You may have noticed that one of the features of all of our replication reports is the “Study Diagram” near the top.  Our Study Diagrams lay out the hypotheses, exactly what participants did in the study, the key findings, and whether those findings replicated. 

Why create a Study Diagram?

We create a Study Diagram for each of our reports because we believe that readers should be presented with the key points of the hypotheses, methods, and results in a consistent format that can be understood at a glance. We do this because clear communication is essential to the scientific process functioning well.

Too often in the research literature key pieces of information are spread throughout the text of a paper, making it more time-consuming and difficult to get a clear overall picture of a study. Sometimes the paper itself doesn’t include all of the necessary information, and readers have to refer to supplemental materials to understand what was actually done. This makes it harder for people to find relevant studies, evaluate their claims, and put the information in them to use.

In contrast, imagine a world in which all published empirical research had a Study Diagram. Understanding the gist of a paper would be faster because the Study Diagram takes much less time to review than the whole paper, while also being more standardized and informative than a typical abstract. The Study Diagram would improve the clarity of published research, making it easier to evaluate how well the claims made in the paper correspond to what is being done in the study itself. This would make it easier to identify possible overclaiming or validity issues that can be signs of Importance Hacking. Finally, it would become much easier to sort through literature to find studies that are relevant to your question. At a glance you would be able to compare key features of studies, like their sample size, exclusion criteria, and whether participants were randomly assigned to conditions.

Our goal at Transparent Replications is to incentivize practices that improve quality and robustness of psychology research. We see Study Diagrams as one of those best practices, and would like to see them become widely adopted in the field.

If you’d like to include a Study Diagram in your research, the sections below walk you through how to create one.

How to diagram a study

Here’s an example study diagram from Report #7:

The Study Diagram is in three parts:

• Hypotheses – a few sentences in plain language explaining the main hypotheses being tested in the study.
• Flowchart of the study – the core of the diagram including information about participants, conditions, study tasks, and exclusions.
• Table of findings – a list of results for the key findings.

Making the flowchart of the study

Participants

The first box includes the number of participants, type of participants, and how they participated.

Although this is typically straightforward, here are two things to pay attention to when reporting on participants:

• Sample criteria filtering and stratifying – If a sample is limited by certain characteristics, this box is where that information belongs. If an eligibility filter is being used to only collect data from certain subgroups of the population, or to collect a certain number of participants in certain categories, that information also belongs here.

• Completed vs. started – Depending on the task and the method being used for data collection it may make sense to report only the number of participants who completed the task, or all of the participants who started the task whether they completed it or not. Either option can be reasonable, but make sure to pay attention here so that the number you are reporting is accurate.

Here’s an example from Report #10 for a study with only one experimental condition, but with more complex requirements for participants:

Study tasks

The next section outlines the tasks that participants did in the study. This section might be one box or a few boxes depending on the complexity of the experimental design. The example diagrams above are for a study with simple randomization to two experimental conditions, and a study with a single condition. The example below is from Report #6 for a study with more complex randomization to multiple conditions:

This section always starts with any initial parts of the experiment that all participants see or complete. Then it goes into the main task which, for studies with multiple conditions, is represented by boxes side-by-side showing what participants in each condition see and do. Finally, if there are parts of the experiment that all participants see or do after the main task, those are presented.

Exclusions

This is the final box of the flowchart, and it reports the number of participants whose data were included in the analysis. It also indicates why other participants were excluded. If participants who completed the study are reported in the first box, then the only exclusions reported here are people who completed the study whose data was not used for some other reason, such as not meeting eligibility criteria. If all participants who started the study are reported in the first box, the number of people who started the study but didn’t complete it would also be reported here.

Making the table of findings

The final section of the Study Diagram is the table of findings. The purpose of this table is to allow the reader to see at a glance what the study tested, and whether the results matched those expectations or not.

Determining what to include in this table can be a bit nuanced. Often there are more results calculated and reported in a paper than would be considered main findings, and including those additional results in this table can make it more difficult for readers to get the high-level overview that the Study Diagram is meant to provide. For example, results related to a manipulation check probably shouldn’t be included in this table. Additionally, if there are multiple statistical tests that pertain to the same claim, reporting those as part of a single row might make sense. 

This first column lists each main claim that was tested, and the later columns present the findings in a simplified way. Typically those findings should be represented with a single word (like “more,” “less,” or “equivalent”) or with a single symbol such as +, -, or 0 to indicate a positive, negative, or null result. With our replication studies, we focus on whether the result from the original study replicated, so the table is designed to make it easy to see if the first column and the second column match. In the case of a study that isn’t a replication, but has pre-registered hypotheses, the table would have a column for the prediction that was made before data collection, and a column for the result. If there were no predictions made in advance, the table would just report the main findings.

What isn’t included in the diagram

You may have noticed that the Study Diagram doesn’t include information about how the statistical tests were conducted. The diagram also doesn’t include actual numerical findings. When we were developing this tool, we determined that it was simply not feasible to include that information while keeping the diagram manageable and understandable. The Study Diagram is not meant to be a replacement for the entire paper.

The Study Diagram gives the reader a quick overview of what participants did and what claims were tested on that basis. The body of the paper is a better place for the level of detail required to explain the statistical methods used, and provide the detailed numerical results.

This means that the Study Diagram is a good starting point for evaluating a study, but determining whether one should have confidence in the reported findings will, of course, continue to require going beyond this tool.

Executive Summary

Transparency	Replicability	Clarity
	0 of 1 findings replicated*

We ran a replication of the experiment from this paper which found that as women were exposed to more images of thin bodies, they were more likely to consider ambiguous bodies to be overweight. The finding was not replicated in our study, but this isn’t necessarily evidence against the hypothesis itself.

The study asked participants to make many rapid judgments of pictures of bodies. The bodies varied in body mass index (BMI) with a range from emaciated to very overweight. Each body was judged by participants as either “overweight” or “not overweight”. Participants were randomized into two conditions: “increasing prevalence” and “stable prevalence”. The increasing prevalence condition saw more and more thin bodies as the experiment progressed. Meanwhile, stable prevalence participants saw a consistent mixture of thin and overweight bodies throughout the experiment. The original study found support for their first hypothesis; compared to participants in the stable prevalence condition, participants in the increasing prevalence condition became more likely to judge ambiguous bodies as “overweight” as the experiment continued. The original paper also examined two additional hypotheses about body self-image judgements, but did not find support for them – we did not include these in our replication.

The original study received a high transparency rating due to being pre-registered and having publicly available data, experimental materials, and analysis code, but could have benefitted from more robust documentation of its exclusion criteria. The primary result from the original study failed to replicate; however, this failure to replicate is likely due to an experimental design decision that made the study less sensitive to detecting the effect than anticipated. The images with BMIs in the range where the effect was most likely to occur were shown very infrequently in the increasing prevalence condition. As such, it may not constitute substantial evidence against the hypothesis itself. The clarity rating could have been improved by discussing the implications of hypotheses 2 and 3 having non-significant results for the paper’s overall claims. Clarity could also have been improved by giving the reader more information about the BMIs of the body images shown to participants and the implications of that for the experiment.

Full Report

Study Diagram

Replication Conducted

We ran a replication of the main study from: Devine, S., Germain, N., Ehrlich, S., & Eppinger, B. (2022). Changes in the prevalence of thin bodies bias young women’s judgments about body size. Psychological Science, 33(8), 1212-1225. https://doi.org/10.1177/09567976221082941

How to cite this replication report: Transparent Replications by Clearer Thinking. (2024). Report #11: Replication of a study from “Changes in the prevalence of thin bodies bias young women’s judgments about body size” (Psychological Science | Devine et al., 2022) https://replications.clearerthinking.org/replication-2022psci33-8

Key Links

• Our Research Box for this replication report includes the pre-registration, de-identified data, and analysis files.
• Our GitLab repository for this replication report includes the code for running the experiment.

Overall Ratings

To what degree was the original study transparent, replicable, and clear?

Transparency:  how transparent was the original study?	All materials were publicly available or provided upon request, but some exclusion criteria deviated between pre-registration and publication.
Replicability: to what extent were we able to replicate the findings of the original study?	The original finding did not replicate. Our analysis found that the key three-way interaction between condition, trial number, and size was not statistically significant. In this case, lack of replication is likely due to an experimental design decision that made the study less sensitive to detecting the effect than was anticipated, rather than evidence against the hypothesis itself. This means that the original simulated power analysis underestimated the sample size needed to detect the effect with this testing procedure.
Clarity: how unlikely is it that the study will be misinterpreted?	The discussion accurately summarizes the findings related to hypothesis 1 but does not discuss potential implications of lack of support for hypotheses 2 and 3.It is easy to misinterpret the presentation of the spectrum of stimuli used in the original experiment as they relate to the relative body mass indexes of the images shown to participants. Graphical representations of the original data only include labels for the minimum and maximum model sizes, making it difficult to interpret the relationship between judgements and stimuli. The difficulty readers would have determining the thin/overweight cutoff value, and the range of results for which judgements were ambiguous from the information presented in the paper could leave readers with misunderstandings about the study’s methods and results.

Detailed Transparency Ratings

Overall Transparency Rating:
1. Methods Transparency:	All materials are publicly available. There were some inconsistencies between the exclusion criteria reported in the paper, supplemental materials, and analysis code provided. We were able to determine the exact methods and rationale for the exclusion criteria through communication with the original authors.
2. Analysis Transparency:	Analysis code is publicly available.
3. Data availability:	The data are publicly available.
4. Preregistration:	We noted two minor deviations from pre-registered exclusion criteria: The preregistration indicated that participants would be excluded if they record 5 or more trial responses where the time between the stimulus display and participant response input is greater than 7 seconds. This criteria diverges slightly from both the final supplemental exclusion report and the exclusions as executed in the analysis script. Additionally, The preregistration indicated that participants with greater than 90% similar judgements across their trials would be excluded. One participant who met this criteria was included in the final analysis. Overall, these inconsistencies are minor and likely had no bearing on the results of the original study.

Summary of Study and Results

Both the original study (n = 419) and our replication (n = 201) tested for evidence of the cognitive mechanism prevalence-induced concept change as an explanation for shifting body type ideals in the context of women’s body image judgments. 

The original paper tested 3 main hypotheses, but only found support for the first hypothesis. Since the original study didn’t find support for hypotheses 2 or 3, our replication focused on testing hypothesis 1: “…if the prevalence of thin bodies in the environment increases, women will be more likely to judge other women’s bodies as overweight than if this shift did not occur.” Our pre-registration of our analysis plan is available here. 

Prevalence-induced concept change happens when a person starts seeing more and more cases of a specific conceptual category. For example, we can consider hair color. Red hair and brown hair are two different conceptual categories of hair color. Some people have hair that is obviously red or obviously brown, but there are many cases where it could go either way. We might call these in-between cases “auburn” or “reddish-brown” or even “brownish-red”. If a person starts seeing many many other people with obviously red hair, then they might start thinking of auburn hair as obviously brown. Their conceptual class of “red hair” has shrunk to exclude the ambiguous cases. 

To test prevalence induced concept change in women’s body image, both the original study and our replication showed participants computer-generated images of women’s bodies and asked participants to judge whether they thought any given body was “overweight” or “not overweight”. The image library included 61 images, ranging from a BMI minimum of 13.19 and a maximum BMI of 120.29. Each participant was randomly assigned to one of two conditions: stable-prevalence or increasing-prevalence. Stable-prevalence participants saw an equal 50/50 split of images of bodies with BMIs above 19.79 (the “overweight” category)¹ and images of bodies with BMIs below 19.79 (the “thin” category). Increasing-prevalence participants saw a greater and greater proportion of bodies with BMIs below 19.79 as the experiment proceeded. If participants in the increasing-prevalence condition became more likely to judge thin or ambiguous bodies as overweight in the later trials of the experiment, compared to participants in the stable-prevalence condition, that would be evidence supporting the hypothesis of prevalence-induced concept change affecting body image judgements.

Overview of Main Task

During the task, participants were shown an image of a human body (all images can be found here). The body image stimulus displays on screen for 500 milliseconds (half of a second), followed by 500 milliseconds of a blank screen and finally a question mark, indicating to participants that it is time to input a response. Participants then recorded a binary judgment by pressing the “L” key on their keyboard to indicate “overweight” or by pressing the “A” key to indicate “not overweight”. Judgements were meant to be made quickly, between 100 and 7000 milliseconds, for each trial. This process was repeated for 16 blocks of 50 iterations each, meaning that each participant recorded 800 responses. 

Additionally, participants completed a self-assessment once before and once after the main task. For this assessment, participants chose a body image from the stimulus set which most closely resembled their own body. Participants were asked to judge the self-representative body from their first self-assessment as “overweight” or “not overweight” before completing their second and final self-assessment. These self-assessments were used for testing hypothesis 2, hypothesis 3, and the exploratory analyses in the original paper. We focused on hypothesis 1 so did not include self-assessment data in our analysis.

Figure 1: Example frames from the task

A (Introduction)

B (Example instruction frame)

C (Block 1 start)

D (Stimulus display [500ms])

E (Prompt to respond)

Results

The original study found a significant three-way interaction between condition, trial, and size (β = 3.85, SE = 0.38, p = 1.09 × 10⁻²³), meaning that participants were more likely to judge ambiguous bodies as “overweight” as they were exposed to more thin bodies over the course of their trials. Our replication, however, did not find this interaction to be significant (β = 0.53, SE = 1.81, p = 0.26). Although it was not significant, the effect was in the correct direction, and the lack of significance may be due to an experimental design decision resulting in lower-than-estimated statistical power. 

Study and Results in Detail

Main Task in Detail

Both the original study and our replication began with a demographic questionnaire. In our replication, the demographic questionnaire from the original study was pared down to only include questions relevant for exclusion criterion and a potential supplemental analysis regarding the original hypothesis 3. The maintained questions are listed below.

• What is your gender?
  • Options: Female, Male, Transgender, Non-Binary
• What is your age in years?
• For statistical purposes, what is your weight?
• For statistical purposes, what is your height?
• Please enter your date of birth.
• Please enter your (first) native language.

We included an additional screening question to ensure recruited participants were able to complete the task.

• Are you currently using a device with a full keyboard?
  • Options: “Yes, I am using a full keyboard”, “No”

The exact proportion of bodies under 19.79 BMI presented out of the total bodies per block for each condition are detailed in Figure 2. Condition manipulations relative to stimuli BMI can be seen in Figure 3. 

Figure 2: Stimuli Prevalence by Condition and Block, Table

	Proportion of thin body image stimuli
Block #	Increasing Prevalence	Stable Prevalence
1	0.50	0.50
2	0.50	0.50
3	0.50	0.50
4	0.50	0.50
5	0.60	0.50
6	0.72	0.50
7	0.86	0.50
8	0.94	0.50
9	0.94	0.50
10	0.94	0.50
11	0.94	0.50
12	0.94	0.50
13	0.94	0.50
14	0.94	0.50
15	0.94	0.50
16	0.94	0.50

Figure 3: Estimated BMI of Stimuli and World Health Organization Categories

Stimulus	Categorization for Study Conditions	BMI	WHO Classification**
T300	Thin	13.19	Thin
T290	Thin	13.38	Thin
T280	Thin	13.47	Thin
T270	Thin	13.77	Thin
T260	Thin	13.86	Thin
T250	Thin	14.10	Thin
T240	Thin	14.28	Thin
T230	Thin	14.46	Thin
T220	Thin	14.65	Thin
T210	Thin	14.87	Thin
T200	Thin	15.06	Thin
T190	Thin	15.24	Thin
T180	Thin	15.49	Thin
T170	Thin	15.67	Thin
T160	Thin	15.74	Thin
T150	Thin	16.12	Thin
T140	Thin	16.40	Thin
T130	Thin	16.64	Thin
T120	Thin	16.81	Thin
T110	Thin	17.08	Thin
T100	Thin	17.28	Thin
T090	Thin	17.56	Thin
T080	Thin	17.77	Thin
T070	Thin	18.01	Thin
T060	Thin	18.26	Thin
T050	Thin	18.50	Normal Range
T040	Thin	18.77	Normal Range
T030	Thin	19.1	Normal Range
T020	Thin	19.3	Normal Range
T010	Thin	19.61	Normal Range
N000	NA*	19.79	Normal Range
H010	Overweight	21.55	Normal Range
H020	Overweight	23.35	Normal Range
H030	Overweight	25.37	Overweight
H040	Overweight	27.37	Overweight
H050	Overweight	29.57	Overweight
H060	Overweight	31.84	Overweight
H070	Overweight	34.13	Overweight
H080	Overweight	36.58	Overweight
H090	Overweight	39.10	Overweight
H100	Overweight	41.76	Overweight
H110	Overweight	44.55	Overweight
H120	Overweight	47.37	Overweight
H130	Overweight	50.23	Overweight
H140	Overweight	53.21	Overweight
H150	Overweight	56.26	Overweight
H160	Overweight	59.31	Overweight
H170	Overweight	62.64	Overweight
H180	Overweight	66.04	Overweight
H190	Overweight	69.56	Overweight
H200	Overweight	73.30	Overweight
H210	Overweight	76.95	Overweight
H220	Overweight	80.98	Overweight
H230	Overweight	85.49	Overweight
H240	Overweight	89.89	Overweight
H250	Overweight	94.40	Overweight
H260	Overweight	99.27	Overweight
H270	Overweight	104.4	Overweight
H280	Overweight	109.45	Overweight
H290	Overweight	114.82	Overweight
H300	Overweight	120.29	Overweight

Data Collection

Data were collected using the Positly recruitment platform and the Pavlovia experiment hosting platform. Data collection began on the 15th of May, 2024 and ended on the 5th of August, 2024.

In consultation with the original authors we determined that a sample size of 200 participants after exclusions would provide adequate statistical power for this replication effort. In the simulations for the original study the authors determined that 140 participants would provide 89% power to detect their expected effect size for hypothesis 1. Typically for replications we aim for a 90% chance to detect an effect that is 75% of the size of the original effect size. To emulate that standard for this study we decided on a sample of 200 participants. It is important to note that the original study had 419 participants after exclusions. This final sample size for the original study was set by simulation-based power analyses for hypotheses 2 and 3 requiring a sample size of ~400 participants for adequate statistical power. Because our replication study did not test hypotheses 2 and 3–since they weren’t supported in the original analysis–we did not need to power the study based on those hypotheses.

While a sample size of 200 subjects was justified at the time, we later learned that the original simulation-based power analysis relied on faulty assumptions, which could only be determined from the empirical data in the original sample. The sample size needed to provide adequate statistical power for hypothesis 1 was underestimated. Because the original study used a larger sample size to power hypotheses 2 and 3, the underestimate of the sample size needed for hypothesis 1 wasn’t detected. As a result, our replication study may have been underpowered.

Excluding Participants and/or Observations

For participants to be eligible to take part in the study, they had to be:

1. Female
2. Aged 18-30
3. English speaking

After data collection, participants were excluded from the analysis under the following circumstances:

1. Participants who took longer than 7 seconds to respond in more than 10 trials.
2. Participants who demonstrated obviously erratic behavior e.g. repeated similar responses across long stretches of trials despite variation in stimuli (see Additional Information about the Exclusion Criteria appendix section).
3. Participants who did not complete the full 800 trials.
4. Participants who do not meet the eligibility criteria.

Additionally, at the suggestion of the original authors, we excluded any observations in which the response was given more than 7 seconds after the display of the stimulus.

249 participants completed the main task. 8 participants did not have their data written due to technical malfunctions (these participants were still compensated as usual). 8 participants were excluded for reporting anything other than “Female” for their gender on the questionnaire. 23 participants were excluded for being over 30 years old. 6 participants were excluded for taking longer than 7 seconds to respond on more than 10 trials. 4 participants were excluded for obviously erratic behavior. Note that some participants fall into two or more of these exclusion categories, so the sum of exclusions listed above is greater than the total number of excluded participants.

Analysis

Both the original paper and our replication utilized a logistic multilevel model to assess the data:

Y_ij = 𝛽_0j + 𝛽_1jTrial_ij + 𝛽_2jSize_ij + 𝛽_3j(Trial_ij x Size_ij)

𝛽_0j = Ɣ₀₀ +  Ɣ₀₁ Condition_j + U_oj

𝛽_1j =  Ɣ₁₀ + Ɣ₁₁ Condition_j + U_1j

𝛽_2j = Ɣ₂₀ + Ɣ₂₁Condition_j

𝛽_3j = Ɣ₃₀ + Ɣ₃₁Condition_j

Where Size is the ordinal relative BMI of computerized model images. That is, the degree to which each body image stimulus is thin or overweight. 

Y_ij represents the log odds of participant j making an “overweight” judgment for trial i. 

U_oj are random intercepts per participant. U_1j are random slopes per participant. Ɣ_xx represents fixed effects. 

Results in Detail

The original study found a significant three-way interaction between condition, trial number, and size (β = 3.85, SE = 0.38, p = 1.09 × 10⁻²³), indicating that as the prevalence of thin bodies in the environment increased, participants were more likely to judge ambiguous bodies (not obviously overweight and not obviously underweight) as overweight. The authors note that this effect is restricted to judgements of “thin and average-size stimuli” due to the increasing-prevalence condition requiring a low frequency of “overweight” stimuli. 

Figure 4: Original Results Table

Predictors	Log Odds	95% CI	p
Intercept	-1.90	-2.01 – -1.78	<0.001
Condition	0.08	-0.04 – 0.20	0.173
Trial0	-0.62	-0.77 – -0.47	<0.001
Size0	21.21	20.82 – 21.59	<0.001
Condition x Trial0	-0.65	-0.81 – -0.50	<0.001
Condition x Size0	-0.48	-0.85 – -0.11	0.011
Trial x Size0	2.05	1.26 – 2.85	<0.001
Condition x Trial0 x Size0	3.85	3.10 – 4.61	<0.001

Figure 5: Original Results Data Representations

From “Changes in the prevalence of thin bodies bias young women’s judgments about body size,” by Devine, S., Germain, N., Ehrlich, S., & Eppinger, B., 2022, Psychological Science, 33(8), 1212-1225.

Figure 6: Replication Results Table

Predictors	Log Odds	95% CI	p
Intercept	-1.59	-1.73–-1.45	<0.001
Condition	0.15	0.2–0.29	0.028
Trial0	-0.80	-0.99–-0.61	<0.001
Size0	20.01	19.50–20.51	<0.001
Condition x Trial0	-0.68	-0.87–-0.49	<0.001
Condition x Size0	-0.43	-0.91–0.06	0.084
Trial x Size0	-0.24	-1.19–0.71	0.626
Condition x Trial0 x Size0	0.53	-0.38–1.43	0.255

Figure 7: Replication Results Data Representation

Interpreting the Results

The failure of this result to replicate is likely to be due to characteristics of the study design that made the experiment a less sensitive test of the hypothesis. For that reason the failure of this study to replicate should not be taken as strong evidence against the original hypothesis that prevalence induced concept change occurs for body images.

The main study design issue that could possibly account for the non-replication of the results is the categorization of “thin” and “overweight” images for the condition manipulation: “thin” images were 19.61 BMI and below, and “overweight” images were 21.55 BMI and above. This low threshold means that participants in the increasing prevalence condition would have seen a very small number of images of bodies that were in the ambiguous or normal range of BMI in which prevalence induced concept change is most likely to occur. Unfortunately, we did not notice this issue with the BMI cutoff between the thin and overweight groups until after we had collected the replication data. This means that our replication, while having the benefit of being faithful to the original study, has the drawback of being affected by the same study design issue.

We presented this issue to the authors after determining that it may explain the lack of replication. The authors explained their rationale for setting the image cutoff at the baseline image:

“In designing the study, we anticipated the most “ambiguous” stimuli to be those near the reference image (BMI of 19.79; the base model). This was based on two factors. First, WHO guidelines suggest that a “normal” BMI lies between 18.5 and 24.9—hence a BMI of 19.79 fell nicely within this range and, as mentioned, allowed for a clean division of the stimulus set into two equal categories. Second, irrespective of the objective BMI, we anticipated participants would judge the reference image as maximally ambiguous in the context of the stimulus set, owing to the range available to participants’ judgements when completing the experiment. Accordingly, the power analysis we conducted was based on this assumption that responses most sensitive to PICC would be those to images near in size to the reference image. But this turned out not to be the case when we acquired the data from our sample. As you point out, increased sensitivity to PICC was at a slightly higher (and evidently under-sampled) range of size (BMI 23.35 – 31.84). As such, the sample size required to detect effects in these ranges with sufficient power may be higher than previously thought.” (Devine, email communication 9/11/24) 

Understanding the Categorization Used

It took us some time to recognize this issue because the original paper does not clearly explain how the “thin” and “overweight” image categories correspond to BMI values of the images, and none of the figures in the original paper show BMI values along the axes representing image sizes. From the paper alone it is not possible for a reader to determine what BMI values the stimuli presented correspond to, with the exception of the endpoints. The paper says: 

Specifically, the proportion of thin to overweight bodies had the following order across each block in the increasing-prevalence condition: .50, .50, .50, .50, .60, .72, .86, .94, .94, .94, .94, .94, .94, .94, .94, .94. In the stable-prevalence condition, the proportion of overweight and thin bodies in the environment did not change; it was always .50 (see Fig. 1b). Bodies were categorized as objectively thin or overweight by Moussally et al. (2017) according to World Health Organization (1995) guidelines. Body mass index (BMI) across all bodies ranged from 13.19 (severely underweight) to 120.29 (very severely obese). (Devine et al, 2022) [Bold italics added for emphasis]

From the information provided in the paper, a reader would be likely to assume that the images in the “overweight” category had BMIs of greater than 25, because a BMI of 25 is the dividing line between “healthy/normal” and “overweight” according to the WHO. Another possible interpretation of this text in the paper would suggest that the bodies that were categorized as thin and/or median in the Moussally et al. (2017) stimulus validation paper were the ones increasing in prevalence in that condition, and those categorized as overweight in the validation study were diminishing in prevalence. Either of these likely reader assumptions would also be supported by the presentation of the results in the original paper:

Most importantly, we found a three-way interaction between condition, trial, and size (β = 3.85, SE = 0.38, p = 1.09 × 10−23). As seen in Figure 2a, this result shows that when the prevalence of thin bodies in the environment increased over the course of the task, participants judged more ambiguous bodies (average bodies) as overweight than when the prevalence remained fixed. We emphasize here that this effect is restricted to judgments of thin and average-size stimuli because the nature of our manipulation reduced the number of overweight stimuli seen by participants in the increasing-prevalence condition (as reflected by larger error bars for larger body sizes in Fig. 2a).  (Devine et al, 2022) [Bold italics added for emphasis]

Moussally et al. developed the stimuli that were used in this study by using 3D modeling software. They started with a default female model (corresponding to 19.79 BMI according to their analysis), scaling down from that default model in 30 increments of the modeling software’s “thin/heavy” dimension to get lower BMIs (down to a low of 13.9), and then scaling up from that default model by 30 increments to get higher BMIs (up to a high of 120.29). They then validated the image set by asking participants to rate images on a 9 point Likert scale where 1 = “fat” and 9 = “thin”. Based on those ratings they established three categories for body shape: “thin, median, or fat.”

Figure 8: Ratings of Body Shape for all Stimuli from Moussally et al. (2017)

Stimulus	BMI	Mean Rating (Likert 1-9)	Validation Study Classification
T300	13.19	8.94	Thin
T290	13.38	8.95	Thin
T280	13.47	8.97	Thin
T270	13.77	8.88	Thin
T260	13.86	8.91	Thin
T250	14.10	8.86	Thin
T240	14.28	8.77	Thin
T230	14.46	8.70	Thin
T220	14.65	8.63	Thin
T210	14.87	8.67	Thin
T200	15.06	8.59	Thin
T190	15.24	8.56	Thin
T180	15.49	8.37	Thin
T170	15.67	8.18	Thin
T160	15.74	8.22	Thin
T150	16.12	8.11	Thin
T140	16.40	8.12	Thin
T130	16.64	8.05	Thin
T120	16.81	7.95	Thin
T110	17.08	7.90	Thin
T100	17.28	7.79	Thin
T090	17.56	7.90	Thin
T080	17.77	7.79	Thin
T070	18.01	7.88	Thin
T060	18.26	7.74	Thin
T050	18.50	7.84	Thin
T040	18.77	7.76	Thin
T030	19.1	7.74	Thin
T020	19.3	7.78	Thin
T010	19.61	7.50	Thin
N000	19.79	7.63	Thin
H010	21.55	7.28	Thin
H020	23.35	6.21	Median
H030	25.37	5.65	Median
H040	27.37	5.26	Median
H050	29.57	4.85	Median
H060	31.84	4.28	Median
H070	34.13	3.63	Fat
H080	36.58	3.62	Fat
H090	39.10	3.10	Fat
H100	41.76	2.78	Fat
H110	44.55	2.65	Fat
H120	47.37	2.45	Fat
H130	50.23	2.32	Fat
H140	53.21	2.02	Fat
H150	56.26	1.95	Fat
H160	59.31	1.68	Fat
H170	62.64	1.56	Fat
H180	66.04	1.59	Fat
H190	69.56	1.44	Fat
H200	73.30	1.45	Fat
H210	76.95	1.30	Fat
H220	80.98	1.23	Fat
H230	85.49	1.17	Fat
H240	89.89	1.16	Fat
H250	94.40	1.11	Fat
H260	99.27	1.06	Fat
H270	104.4	1.09	Fat
H280	109.45	1.10	Fat
H290	114.82	1.06	Fat
H300	120.29	1.05	Fat

The “median” images according to the judgements reported in Moussally et. al. (2017) ranged from a BMI of 23.35 to 31.84; however, neither of those cutoffs nor the commonly used WHO BMI guideline of 25 and above as “overweight” were used to set the cutoff between the groups of “thin” and “overweight” images in the experiment we replicated. From looking at the study code itself, this study used the 30 images scaled down from the baseline image of 19.79 BMI as the “thin” group and the 30 images scaled up from the baseline as the “overweight” group. The 19.79 BMI image was not included in either group, so it was not presented to participants in the experiment. That means that the “thin” images that were increasing in prevalence ranged from a BMI of 13.19 to 19.61, and the “overweight” images that were decreasing in prevalence ranged from a BMI of 21.55 to 120.29. The 21.55 BMI image was categorized as “thin” in the Moussally et al. (2017) validation study, and is well within the normal/healthy weight range according to the WHO, and yet it was categorized with the “overweight” images in this study. This 21.55 BMI image was judged as “not overweight” for 96% of trials in the original dataset for the present study, further suggesting that the experiment’s cutoff between “thin” and “overweight” was placed at too low of a BMI to adequately capture data for ambiguous body images.

Implications of the Categorization

Figure 2b in the original paper presents the results for a BMI of 23.35, which is within the “normal/healthy” range according to the WHO, and is the lowest BMI “median” image according to the validation study. This is clearly meant to be one of the normal or ambiguous body sizes for which prevalence induced concept change would be most expected. The inclusion of this image in the “overweight” grouping for which the prevalence was decreasing means this image would not have been shown to participants very often. The caveat in the results section that “this effect is restricted to judgments of thin and average-size stimuli because the nature of our manipulation reduced the number of overweight stimuli seen by participants in the increasing-prevalence condition,” applies to the 23.35 BMI image that is presented in the paper as a demonstration of the effect.

In the last 200 trials in the increasing prevalence condition only 6% of the images presented would have been from the set of 30 “overweight” images. That means that each participant only saw 12 presentations of “overweight” images in the last 200 trials. Each individual subject in the increasing prevalence condition would only have had an approximately 33% chance of seeing the BMI 23.35 image at least once during the last 200 trials. Ideally, this image–and others in the ambiguous range–should be shown much more frequently in order to capture possible effects of prevalence induced concept change.

In the original study, looking at the last 200 trials, the 23.35 BMI image was presented only 80 times out of 42,600 image presentations to the increasing prevalence condition. In the replication study, looking at the last 200 trials, that image was only presented 51 times out of 20,000 image presentations to the increasing prevalence condition.

Figure 9 below shows how many times stimuli of BMI values 18.77 – 31.84 were presented and what percentage of them were judged as “overweight”  in the last 200 trials in each condition across all subjects for the original dataset and the replication dataset. The rows that are color coded by condition and have BMI values in bold are from the “overweight” group.

Figure 9: Data Presentation Frequency and % “Overweight” judgements in last 200 trials

A (Original Data)

	Increasing (N = 213)		Stable (N = 206)
Stimulus (BMI)	Number of presentations (out of 42,600)	% Judged as “Overweight”	Number of presentations (out of 41,200)	% Judged as “Overweight”
18.77	1337	2.99%	701	2.28%
19.1	1365	4.03%	673	2.23%
19.3	1288	3.80%	718	1.39%
19.61	1334	3.97%	698	2.72%
21.55	73	8.22%	676	3.40%
23.35	80	25.00%	685	9.78%
25.37	81	28.40%	687	21.83%
27.37	96	43.75%	683	34.85%
29.57	93	53.76%	726	52.07%
31.84	83	61.45%	710	56.90%

B (Replication Data)

	Increasing (N = 100)		Stable (N = 101)
Stimulus (BMI)	Number of presentations (out of 20,000)	% Judged as “Overweight”	Number of presentations (out of 20,100)	% Judged as “Overweight”
18.77	611	0.82%	315	2.22%
19.1	590	2.03%	333	2.40%
19.3	634	2.05%	314	2.55%
19.61	631	2.06%	319	2.19%
21.55	41	7.32%	331	4.53%
23.35	51	15.69%	336	10.71%
25.37	41	34.15%	357	24.93%
27.37	35	42.86%	315	35.56%
29.57	35	68.57%	346	52.89%
31.84	42	59.52%	385	58.70%

From looking at these tables, it’s easy to see that in both conditions only a small percentage of the stimuli from 18.77 to 19.61 BMI were judged to be overweight. There is much more variation in judgment in the 21.55 to 31.84 BMI images, but the number of times those were presented in the increasing prevalence condition was very small. The fact that the most important stimuli for demonstrating the proposed effect were presented extremely infrequently in the study likely undermines the reliability of this test of the prevalence induced concept change hypothesis by making it much less sensitive to detecting whether the effect is present.

Implications of Nonreplication for the Prevalence Induced Concept Change Hypothesis

If we look more closely at the results for the range of BMI values for which there is ambiguity in both the original data and the replication data we can see that the pattern of results for those values looks similar.

Figure 10: Data for the last 200 trials

A (Original Data)

B (Replication Data)

Figure 10 above shows that only one datapoint in the replication data has results that are clearly outside of the margin of error (BMI = 29.57), but the pattern looks similar to what we see in the original data. This suggests that despite the issues with the experimental design, the original study may have been able to detect an effect because it was much more highly powered than should have been necessary to test this hypothesis due to the need for a higher statistical power for hypotheses 2 and 3 in the original paper. In the replication study, which was powered appropriately according to the original study’s simulation analysis, the effective power was lower than what was simulated due to the miscategorization of the ambiguous images into the overweight group.

Proposed Experimental Design Changes

In our view, a better threshold between the “thin” and “overweight” images for testing this hypothesis would be 31.84 (the high end of the “median” range reported in the Moussally et. al. (2017) paper). This threshold would ensure that participants are presented with many opportunities to judge the images that are in the ambiguous range where prevalence induced concept change is most likely to be observed. Shifting to this threshold would make this experiment better suited to detecting the hypothesized effect.

Additionally, this experiment would benefit from having more stimuli that are in the ambiguous range of values – i.e. more stimuli with BMIs between 23.35 and 31.84. In this study only 5 of the images (23.35, 25.37, 27.37, 29.57, 31.84) are in the range Moussally et al. determine to be “median.” A larger set of stimuli in the ambiguous range would provide more data points in the relevant range for testing the hypothesis. We recognize that this change would require developing and validating additional stimuli, which would be labor-intensive.

Comparing the stimuli used in this study to those used in the Levari et al. (2018) experiment–on which this study is based–provides an illustration that helps explain why this would be important for testing this hypothesis. Levari et al. tested prevalence induced concept change using images of 100 dots that ranged in color from purple to blue. When they decreased the prevalence of blue dots, they found that people were more likely to consider ambiguous dots to be blue. Stimuli from Levari et al.’s paper can be seen in Figure 11c, where there are 18-19 stimuli at color values in between each of the dots shown. From looking at these representative stimuli it’s clear that there were many examples of different stimuli in the range of values that were ambiguous.

Figure 11: Levari et al. (2018) Colored Dots Study 1

A-B (Results visualization)

C (Color spectrum stimuli examples)

Prevalence-induced concept change should be observable mainly in ambiguous stimuli. We expect this effect to be non-existent for the extreme exemplars of the relevant conceptual category. That is, the bluest dots will always be identified as blue, but judgements of ambiguous dots should be susceptible to the effect. Looking at Figures 11a-11b, a substantial fraction of the 100 different dot images were ambiguous (identified as blue some of the time, rather than 100% or 0% of the time). A wide range of ambiguous stimuli make this effect easier to capture. Additionally, these ambiguous dots were clustered on the purple half of the color spectrum. This is important because Levari et al.’s manipulation increased the frequency of the purple-spectrum dots. So, their data contained many observations of ambiguous dots despite the condition manipulation decreasing the frequency of blue-spectrum dots. Compare the above Figures 11a-11b from Levari et al. to the below Figure 12 generated from the original body image study data:

Figure 12: PICCBI Original Results Visualization

It’s not possible to see the curve shift in the increasing prevalence condition here (Figure 12), despite the model having a significant result. This is likely because there are many fewer observations in the ambiguous range of stimuli. This makes the model more sensitive to noise at the extreme values. Looking at these figures for the replication data in Figure 13, we see that noise in the infrequently presented larger BMI images shapes the divergence between the curves in a way that’s not consistent with the hypothesis:

Figure 13: PICCBI Replication Results Visualization

Taking more measurements in the ambiguous range by having more stimulus images with BMI values in that range would improve the ability of this experiment to reliably detect whether prevalence induced concept change occurs for body images.

It’s also worth noting that this issue with the study design was somewhat obscured by the design of the figures presenting the data in the paper. Instead of using the curves above like the Levari et al. (2018) paper used, the data for this study was presented by showing the percentage of overweight ratings for the first 200 trials subtracted from the last 200 trials, as seen in Figure 5. This method highlights the relevant change from the early trials to the later trials, but has the downside of not clearly presenting the actual values. Many of those values didn’t change from the early to the late trials because they were near the ceiling or the floor (almost all judgements were one-way). It was not possible to tell what the actual percentages of overweight judgements were from the information presented in the paper, which meant it was not clear which stimuli had overweight judgements near the ceiling or floor and which were ambiguous. Being able to tell where the ambiguous values were would have been useful to readers attempting to interpret the results of this study.

By incorporating these changes, a new version of this study would shed a lot of light on the question of whether prevalence induced concept change can be reliably detected for body images.

Conclusion

The results of the original paper failed to replicate, which we suspect was due to the experiment being less sensitive to the effect than anticipated. For this reason we emphasize that our findings do not provide strong evidence against the original hypothesis. Prevalence-induced concept change may affect women’s body image judgements, but the present experiment was not as sensitive to detect this effect with the current sample size as previously believed. The design could be improved by raising the BMI cutoff between “thin” and “overweight” images for the prevalence manipulation and/or including additional stimuli within the range of ambiguous body sizes (BMI 23.35 – 31.84) to increase the frequency of ambiguous stimuli, which are the most important for demonstrating a change in concept.

The clarity rating of 2.5 stars was due to two factors. The original discussion section did not address the potential implications of the lack of support for hypotheses 2 and 3. Since hypotheses 2 and 3 related to people applying these changes in the concept of thinness to their own bodies, the lack of support for those hypotheses may limit the claims that should be made about potential real world effects of prevalence induced concept change for body image. Additionally, the difficulty of determining the stimulus BMI values, the thin/overweight cutoff value, and the range of results for which judgements were ambiguous from the information presented in the paper could leave readers with misunderstandings about the study’s methods and results. 

The study had a high transparency rating of 4.5 stars because all of the original data, experiment/analysis code, and pre-registration materials were publicly available. There were minor discrepancies in exclusion criteria based on reaction times between the pre-registration and the analysis, and some documentation for exclusion criteria and code for evaluating participant quality wasn’t publicly posted. However, the undocumented code was provided upon request, and the inconsistency in exclusion criteria was subtle and likely had no bearing on the results.

Author Acknowledgements

We would like to thank the authors of “Changes in the Prevalence of Thin Bodies Bias Young Women’s Judgements About Body Size”: Sean Devine, Nathalie Germain, Stefan Ehrlich, and Ben Eppinger for everything they’ve done to make this replication report possible. We thank them for their original research and for making their data, experiment code, analysis, and other materials publicly available. The original authors provided feedback with expedient, supportive correspondence and this report was greatly improved by their input. 

Thank you to Isaac Handley-Miner for your consultation on multilevel modeling for our analysis. Your expertise was invaluable.

Thank you to Soundar and Nathan from the Positly team for your technical support with the data collection. 

Thank you to Spencer Greenberg for your guidance and feedback throughout the project.

Last, but certainly not least, thank you to all 249 individuals who participated in the replication experiment.

Response from the Original Authors

The original paper’s authorship team offers this response (PDF) to our report. We are grateful for their thoughtful engagement with our report.

Purpose of Transparent Replications by Clearer Thinking

Transparent Replications conducts replications and evaluates the transparency of randomly-selected, recently-published psychology papers in prestigious journals, with the overall aim of rewarding best practices and shifting incentives in social science toward more replicable research.
We welcome reader feedback on this report, and input on this project overall.

Appendices

Additional Information about the Exclusion Criteria

249 participants completed the main task

• 8 participants were excluded due to technical malfunctions.
  • 5 of these participants did not have their data written due to terminating their connection to Pavlovia before the data saving operations could complete. These participants were compensated for completion of the full task.
  • 3 of these participants were excluded for incomplete data sets.These 3 exclusions stand out as unexplained data writing malfunctions. These participants were compensated for completion of the full task, despite the partial datasets. 
• 8 participants were excluded for reporting anything other than “Female” for their gender on the questionnaire. 
• 23 participants were excluded for being over 30 years old. 
• 6 participants were excluded for taking longer than 7 seconds to respond on more than 10 trials. 
• 4 participants were excluded for obviously erratic behavior. 

The “erratic behavior” exclusions were determined by generating graphical representations of individual subject judgements over time and manually reviewing them for signs of unreasonable behavior. The code for generating these individual subject graphs was provided by the original authors and we consulted with the original authors on their assessment of the graphs. The generation code and a complete set of graphics can be found in our gitlab repository. Figure 14a is an example of expected behavior from a participant. They tended to judge very thin stimuli as “not overweight” and very overweight stimuli as “overweight” with some variance, especially around ambiguous stimuli closer to the middle of the spectrum. Figures 14b-14e are the subjects we excluded based on their curves. 14b made judgments exactly opposite the expected behavior for their first 200 trials which indicates that this participant was confused about which key on their keyboard related to which judgment. In 14c, we see that this participant’s judgements in the last 200 trials were completely random. They likely stopped paying attention at some point during the task and assigned judgements randomly. Because this criterion is somewhat subjective, only the most obviously invalid data were excluded. Any participants with questionable but ambiguous curves had their data included to avoid the possibility of biased exclusions.

Figure 14: Individual Subject Curves

A  (Good Subject Curve)

B

C

D

E

References

Devine, S., Germain, N., Ehrlich, S., & Eppinger, B. (2022). Changes in the prevalence of thin bodies bias young women’s judgments about body size. Psychological Science, 33(8), 1212-1225. https://doi.org/10.1177/09567976221082941

Faul, F., Erdfelder, E., Buchner, A., & Lang, A.-G. (2009). Statistical power analyses using G*Power 3.1: Tests for correlation and regression analyses. Behavior Research Methods, 41, 1149-1160. Download PDF

Levari, D. E., Gilbert, D. T., Wilson, T. D., Sievers, B., Amodio, D. M., & Wheatley, T. (2018). Prevalence-induced concept change in human judgment. Science, 360(6396), 1465-1467. https://doi.org/10.1016/j.cognition.2022.105196

Moussally, J. M., Rochat, L., Posada, A., & Van der Linden, M. (2017). A database of body-only computer-generated pictures of women for body-image studies: Development and preliminary validation. Behavior research methods, 49(1), 172-183. https://doi.org/10.3758/s13428-016-0703-7

World Health Organization. (1995). Physical status: The use of and interpretation of anthropometry. Report of a WHO expert committee. https://apps.who.int/iris/handle/10665/37003

1. We are using the category labels “thin” and “overweight” because they were used in the original paper. These labels do not necessarily correspond to what they would mean in everyday usage, and should not be taken as objective measures of health, perception, nor the opinions of the researchers. More information on the decisions behind the categorizations can be found in the Understanding the Categorizations Used section. ↩︎

This is an opinion piece from our founder, Spencer Greenberg.

A significant and pretty common problem I see when reading papers in social science (and psychology in particular) is that they present a fancy analysis but don’t show the results of what we have named the “Simplest Valid Analysis” – which is the simplest possible way of analyzing the data that is still a valid test of the hypothesis in question.

This creates two potentially serious problems that make me less confident in the reported results:

1. Fancy analyses impress people (including reviewers), but they are often harder to interpret than simple analyses. And it’s much less likely the reader really understands the fancy analysis, including its limitations, assumptions, and gotchas. So, the fancy analysis can easily be misinterpreted, and is sometimes even invalid for subtle reasons that reviewers, readers (and perhaps the researchers themselves) don’t realize. As a mathematician, I am deeply unimpressed when someone shows me a complex mathematical method when a simple one would have sufficed, but a lot of people fear or are impressed by fancy math, so complex analyses can be a shield that people hide behind.

2. Fancy analyses typically have more “researcher degrees of freedom.” This means that there is more wiggle room for researchers to choose an analysis that makes the results look the way the researcher would prefer they turn out. These choices can be all too easy to justify for many reasons including confirmation bias, wishful thinking, and a “publish or perish” mentality. In contrast, the Simplest Valid Analysis is often very constrained, with few (if any) choices left to the researcher. This makes it less prone to both unconscious and conscious biases.

When a paper doesn’t include the Simplest Valid Analysis, I think it is wise to downgrade your trust in the result at least a little bit. It doesn’t mean the results are wrong, but it does mean that they are harder to interpret.

I also think it’s fine and even good for researchers to include more sophisticated (valid) analyses and to explain why they believe those are better than the Simplest Valid Analysis, as long as the Simplest Valid Analysis is also included. Fancy methods sometimes are indeed better than simpler ones, but that’s not a good reason to exclude the simpler analysis.

Here are some real-world examples where I’ve seen a fancier analysis used while failing to report the Simplest Valid Analysis:

• Running a linear regression with lots of control variables when there is no need to control for all of these variables (or no need to control for more than one or two of the variables)
• Use of ANOVA with lots of variables when really the hypothesis only requires a simple comparison of two means
• Use of a custom statistical algorithm when a very simple standard algorithm can also test the hypothesis
• Use of fancy machine learning when simple regression algorithms may perform just as well
• Combining lots of tests into one using fancy methods rather than performing each test one at a time in a simple way

The problems that can occur when the results of Simplest Valid Analysis aren’t reported was one of the reasons that we decided to include a Clarity Criterion in our evaluation of studies for Transparent Replications. As part of evaluating a study’s Clarity, if it does not present the results of the Simplest Valid Analysis, we determine what that analysis would be, and pre-register and conduct the Simplest Valid Analysis on both the original data and the new data we collect for the replication. Usually it is fairly easy to determine what the Simplest Valid Analysis would be for a research question, but not always. When there are multiple analyses that could be used as the Simplest Valid Analysis, we select the one that we believe is most likely to be informative, and we select that analysis prior to running analyses on the original data and prior to collecting the replication data.

In my view, while it is very important that a study replicates, replication alone does not guarantee that a study’s results reflect something real in the world. For that to be the case, we also have to be confident that the results obtained are from valid tests of the hypotheses. One way to increase the likelihood of that being the case is to report the results from the Simplest Valid Analysis.

My advice is that, when you’re reading scientific results, look for the Simplest Valid Analysis, and if it’s not there, downgrade your trust in the results at least a little bit. If you’re a researcher, remember to report the Simplest Valid Analysis to help your work be trusted and to help avoid mistakes (I aspire always to do so, though there have likely been times I have forgotten to). And if you’re a peer reviewer or journal editor, ask authors to report the Simplest Valid Analysis in their papers in order to reduce the risk that the results have been misinterpreted.

Executive Summary

Transparency	Replicability	Clarity
	4 of 4 findings replicated

We ran a replication of Study 5b from this paper. This study tested whether people believe that morality is declining over time. 

The paper noted that people encounter disproportionately negative information about current-day people (e.g., via the media) and people often have weaker emotional responses to negative events from the past. As such, the authors hypothesized that participants would think people are less moral today than people used to be, but that this perception of moral decline would diminish when comparing timepoints before participants were born.    

To test these hypotheses, the study asked each participant to rate how “kind, honest, nice, and good” they thought people are today and were at four previous timepoints corresponding, approximately, to when participants were 20 years old, when they were born, 20 years before they were born, and 40 years before they were born.

The results from the original study confirmed the authors’ predictions: Participants perceived moral decline during their lifetime, but there was no evidence of perceived moral decline for the time periods before participants were born. 

Our replication found the same pattern of results.

​​The study received a transparency rating of 4.25 stars because its materials, data, and code were publicly available, but it was not pre-registered. The paper received a replicability rating of 5 stars because all of its primary findings replicated. The study received a clarity rating of 5 stars because the claims were well-calibrated to the study design and statistical results.

Full Report

Study Diagram

Replication Conducted

We ran a replication of Study 5b from: Mastrioanni, A.M., & Gilbert, D.T. (2023). The illusion of moral decline. Nature, 618, 782–789. https://doi.org/10.1038/s41586-023-06137-x 

How to cite this replication report: Transparent Replications by Clearer Thinking. (2024). Report #10: Replication of a study from “The illusion of moral decline” (Nature | Mastroianni & Gilbert 2023) https://replications.clearerthinking.org/replication-2023nature618
(Preprint DOI: https://doi.org/10.31234/osf.io/32xvw)

Key Links

• Our Research Box for this replication report includes the pre-registration, study materials, de-identified data, and analysis files.

Overall Ratings

To what degree was the original study transparent, replicable, and clear?

Transparency: how transparent was the original study?	All materials, analysis code, and data were publicly available. The study was not pre-registered.
Replicability: to what extent were we able to replicate the findings of the original study?	All primary findings from the original study replicated.
Clarity: how unlikely is it that the study will be misinterpreted?	This study is explained clearly, the statistics used for the main analyses are straightforward and interpreted correctly, and the claims were well-calibrated to the study design and statistical results.

Detailed Transparency Ratings

Overall Transparency Rating:
1. Methods Transparency:	The materials were publicly available and complete.
2. Analysis Transparency:	The analysis code was publicly available and complete. We successfully reproduced the results in the original paper from the publicly available code and data.
3. Data availability:	The raw data were publicly available and complete.
4. Preregistration:	The study was not pre-registered.

Summary of Study and Results

Summary of the hypotheses

The original study made two key predictions: 

1. For time periods during study participants’ lifetimes, participants would perceive moral decline. In other words, they would believe people are morally worse today than people were in the past.
2. For time periods before participants were born, participants’ perceptions of moral decline would diminish, disappear, or reverse (relative to the time periods during their lifetimes). 

The original paper argues that these results are predicted by the two features that the authors hypothesize produce perceptions of moral decline: (a) a biased exposure effect whereby people see more negative information than positive information about current-day people (e.g., via the media); (b) a biased memory effect whereby people are less likely to have strong negative emotional responses to negative events from the past.

Summary of the methods

The original study (N=387) and our replication (N=533) examined participants’ perceptions of how moral other people were at different points in time. 

Participants from the following age groups were recruited to participate in the study:

• 18–24
• 25–29
• 30–34
• 35–39
• 40–44
• 45–49
• 50–54
• 55–59
• 60–64
• 65–69

After answering a few pre-study questions (see “Study and Results in Detail” section), participants were told, “In this study, we’ll ask you how kind, honest, nice, and good people were at various points in time. If you’re not sure or you weren’t alive at that time, that’s okay, just give your best guess.”

Participants then completed the five primary questions of interest for this study, reporting how “kind, honest, nice, and good” people were at five different timepoints:

• today (“today”)
• around the year the participant turned 20 (“20 years after birth”) 
• around the year the participant was born (“birth year”)
• around 20 years before the participant was born (“20 years before birth”)
• around 40 years before the participant was born (“40 years before birth”)

Going forward, we will use the terms in parentheses as shorthand for each of these timepoints. But please note that the timepoints asked about were approximate—for example, “birth year” is not the exact year each participant was born, but it is within a 5-year range of each participant’s birth year.

Figure 1 shows the versions of the primary questions that a 50-54 year-old participant would receive. Each question was asked on a separate survey page. Participants in other age groups saw the same general questions, but the number of “years ago” in questions 2-5 was adjusted to their age group. Participants aged 18-24 did not receive the second question because today and 20 years after birth were the same period of time for participants in this age group.

After completing the primary questions of interest, participants completed a consistency-check question, attention-check question, and demographic questionnaire (see “Study and Results in Detail” section).

Summary of the primary results

The original paper compared participants’ average ratings of how “kind, honest, nice, and good” people were between each adjacent timepoint. They found that:

• Participants rated people as less kind, honest, nice, and good today vs 20 years after birth.
• Participants rated people as less kind, honest, nice, and good 20 years after birth vs birth year.
• Participants rated people as equivalently kind, honest, nice, and good at birth year vs 20 years before birth.
• There was no statistically significant evidence of either a difference or equivalence between participants’ ratings of how kind, honest, nice, and good people were 20 years before birth vs 40 years before birth. (However, if anything, participants’ ratings were lower at 40 years before birth, which was consistent with the original paper’s hypotheses.)

See “Study and Results in Detail” section for details on the statistical analyses and model results.

When the original authors reviewed our pre-registration prior to replication data being collected, Dr. Mastroianni offered insights about what results they would be more or less surprised by if we found them in our replication data. Because his comments are from prior to the collection of new data, we and the original authors both thought they added useful context to our report:

As for what constitutes a replication, it’s an interesting question. We ran our studies to answer a question rather than to prove a point, so the way I think about this is, “what kinds of results would make me believe the answer to the question is different from the one I believe now?”

• If Contrast 1 was not significant, this would be very surprising, as it would contradict basically every other study in the paper, as well as the hundreds of surveys we review in Study 1.
• If Contrast 2 was not significant, this would be mildly surprising. Contrast 2 is a direct replication of a significant contrast we also saw in Study 2c (as is Contrast 1, for that matter). But this difference was fairly small both times, so it wouldn’t be completely crazy if it didn’t show up sometimes.
• Contrasts 3 and 4 were pretty flat in the original paper. It would be very surprising if those were large effects in the replication. If they’re significant but very small in either direction, it wouldn’t be that surprising.

Basically, it would be very surprising if people perceive moral decline at both points before their birth, but they perceive moral improvement at both points after their birth. That would really make us scratch our heads. It would be surprising in general if there was more decline in Contrasts 3 & 4 than in 1 & 2.

Dr. Adam Mastroianni in email to Transparent Replications team, 2/29/2024.

Summary of replication results

When we analyzed our data, the results of our replication aligned extremely closely with the results of the original study (compare Figure 2 below to Figure 4 in the original paper).

The only minor difference in the statistical results between the original study and our replication was that our replication found statistically significant evidence of equivalence between participants’ ratings of how kind, honest, nice, and good people were at 20 years before birth versus 40 years before birth. As specified in our preregistration, we still consider this a replication of the original results because it is consistent with the paper’s hypothesis (and subsequent claims) that perceptions of moral decline diminish, disappear, or reverse if people rate time periods before they were born.

Here is a summary of the findings in the original study compared to the replication study:

Morality ratings in original study	Morality ratings in replication study	Replicated?
today < 20 years after birth	today < 20 years after birth	✅
20 years after birth < birth year	20 years after birth < birth year	✅
birth year = 20 years before birth	birth year = 20 years before birth	✅
20 years before birth ? 40 years before birth	20 years before birth = 40 years before birth	✅

Study and Results in Detail

Methods in detail

Preliminary survey questions

Before completing the primary questions of interest in the survey, participants indicated which of the following age groups they belonged to:

• 18–24
• 25–29
• 30–34
• 35–39
• 40–44
• 45–49
• 50–54
• 55–59
• 60–64
• 65–69
• 70+

Participants who selected 70+ were screened out from completing the full survey. The original study recruited nearly equal numbers of participants for each of the other 10 age groups. Our replication attempted to do the same, but did not perfectly recruit equal numbers from each age group (see Appendix for more information). 

Participants also completed three questions that, according to the original paper, were designed to test “English proficiency and knowledge of US American culture”:

Which of the following are not a type of footwear?

• Sneakers 
• Slippers
• Flip-flops 
• High heels 
• Bell bottoms 

Which of the following would be most likely to require an RSVP?

• A wedding invitation 
• A restaurant bill 
• A diploma
• A thank-you note 
• A diary 

Which of the following would be most likely to have a sign that says “out of order”?

• An elevator 
• A person 
• A pizza 
• A book
• An umbrella

Consistency check

After completing the five primary questions of interest described in the “Summary of Study and Results” section above, participants answered the following consistency check question: 

Please choose the option below that best represents your opinion: 

• People are MORE kind, honest, nice, and good today compared to about [X] years ago
• People are LESS kind, honest, nice, and good today compared to about [X] years ago
• People are equally kind, honest, nice, and good today compared to about [X] years ago

“[X]” took on the same value as the final timepoint—around 40 years before the participant was born. This question was designed to ensure that participants were providing consistent ratings in the survey. 

Demographics and attention check

After completing the consistency check question, participants reported their age, gender, race/ethnicity, household income, educational attainment, parental status, and political ideology. 

Embedded among these demographic questions was the following attention-check question:

Some people are extroverted, and some people are introverted. Please select the option “other” and type in the word “apple”.

• Extroverted
• Introverted
• Neither extroverted nor introverted
• Other _______ 

Exclusion criteria

Participants’ responses were excluded from the data if any of the following applied:

• They did not complete the study
• They reported being in the 70+ age group
• They failed any of the three English proficiency questions
• They failed the attention check question
• Their answer to the consistency check question was inconsistent with their ratings for today and 40 years before birth
• Their reported age in the demographics section was inconsistent with the age group they selected at the beginning of the study

Of the 721 participants who took the survey, 533 passed all exclusion criteria and were thus included in our analyses. 

Primary analyses: detailed results

As pre-registered, we ran the same statistical analyses as the original paper. 

To analyze the primary questions of interest, we ran a linear mixed effects model, with random intercepts for participants, testing whether participants’ morality ratings differed by timepoint (using the lmer package in R).

We then tested four specific contrasts between the five timepoints using a Holm-Bonferroni correction for multiple comparisons (using the emmeans package in R):

• today vs 20 years after birth
• 20 years after birth vs birth year
• birth year vs 20 years before birth
• 20 years before birth vs 40 years before birth 

Here are the results of these contrasts:

Contrast	Estimate	SE	df	t-value	p-value
today vs 20 years after birth	-0.727	0.052	2094	-13.915	<0.001***
20 years after birth vs birth year	-0.314	0.052	2094	-6.015	<0.001***
birth year vs 20 years before birth	-0.036	0.051	2088	-0.699	0.485
20 years before birth vs 40 years before birth	0.088	0.051	2088	1.729	0.168

There were statistically significant differences between today and 20 years after birth and between 20 years after birth and birth year, but not between birth year and 20 years before birth or between 20 years before birth and 40 years before birth—the same pattern as the original study results. 

Next, we conducted equivalence tests (using the parameters package in R), for the two comparisons that were not statistically significant. Here are the results:

Contrast	ROPE	90% Confidence Interval	SGPV	Equivalence	p-value
birth year vs 20 years before birth	[-0.13 0.13]	[-0.09, 0.02]	> .999	Accepted	0.003**
20 years before birth vs 40 years before birth	[-0.14, 0.14]	[0.04, 0.14]	> .999	Accepted	0.034*

These tests found that, for both contrasts, 100% of the confidence interval range was inside the region of practical equivalence (ROPE). (See the Appendix for a brief discussion on how the ROPE was determined.) Thus, there was statistically significant evidence that birth year and 20 years before birth were equivalent and that 20 years before birth and 40 years before birth were equivalent. (You can read about how to interpret equivalence test results from the parameters package here.) 

In the original study, birth year and 20 years before birth were found to be equivalent, but there was not statistically significant evidence for equivalence between 20 years before birth and 40 years before birth. As mentioned earlier, we consider equivalence between 20 years before birth and 40 years before birth to be a successful replication of the original study’s findings because it is in line with the claims in the paper that perceptions of moral decline diminish, disappear, or reverse when people are asked about time periods before they were born.

Secondary analyses

As in the original paper, we also tested for relationships between participants’ morality ratings and various demographic variables. Since this analysis was not central to the paper’s claims, we preregistered that these results would not count towards the replicability rating for this paper. 

Following the analytical approach in the original paper, we ran a linear regression predicting the difference in participants’ morality ratings between today and birth year by all of the following demographic variables:

• Age 
• Political ideology
• Parental status
• Gender
• Race/ethnicity 
• Educational attainment

Here are the statistical results from this analysis:

Variable	Original Results (R2 = 0.129)	Replication Results (R2 = 0.128)
Age	-0.014** (0.005)	-0.003 (0.005)
Political ideology	-0.335*** (0.058)	-0.307*** (0.048)
Parental status	0.131 (0.150)	0.345** (0.123)
Gender
– Male vs Female	0.137 (0.139)	0.046 (0.117)
– Other vs Female	0.750 (0.764)	1.610* (0.761)
Race
– American Indian or Alaska Native vs White	n/a	1.635 (0.928)
– Asian vs White	0.061 (0.212)	-0.044 (0.208)
– Black or African-American vs White	-0.289 (0.327)	-0.500 (0.271)
– Hawaiian or Pacific Islander vs White	-2.039 (1.305)	n/a
– Hispanic or Latino Origin vs White	0.006 (0.367)	0.036 (0.265)
– More than 1 of the above vs White	0.546 (0.496)	0.219 (0.344)
– Other vs White	0.535 (1.301)	0.355 (0.926)
Education	-0.012 (0.045)	0.063 (0.037)

We explain the results for each demographic variable below: 

Age

The original study found a statistically significant effect of age such that older people perceived more moral decline (i.e., a larger negative difference between today and birth year morality ratings). However, the original paper argued that this was because the number of years between today and birth year was larger for older participants. 

Our replication did not find a statistically significant effect of age. 

Political ideology

Participants could choose any of the following options for political ideology:

• Very liberal
• Somewhat liberal
• Neither liberal nor conservative
• Somewhat conservative
• Very conservative

We converted this to a numeric variable ranging from -2 (very liberal) to 2 (very conservative). 

The original study found a statistically significant effect of political ideology such that more conservative participants perceived more moral decline. Our replication found the same result. 

Following the original study, we ran a one-sample t-test to determine whether participants who identified as “very liberal” or “somewhat liberal” still perceived moral decline, on average. These participants had an average score of less than zero (mean difference = -0.76, t(295) = -9.6252, p < 2.2e-16), meaning that they did, on average, perceive moral decline. 

Parental status

Participants reported how many children they had. We converted this into a binary variable representing whether or not each participant is a parent. 

The original study did not find a statistically significant effect of parental status. However, our replication found a significant effect such that parents perceived more moral decline than non-parents.

Gender

Participants could choose any of the following options for gender:

• Male
• Female
• Other

The original study did not find a statistically significant effect of gender. Our replication, on the other hand, found a significant effect of gender such that participants who selected “Other” did not perceive moral decline, on average. However, we do not recommend giving much credence to this statistical difference because only 3 out of the 533 participants selected “Other.” We think conclusions should not be drawn in either direction with such a small sample size for that category.

Race/ethnicity

Participants could choose any of the following options for race/ethnicity:

• American Indian or Alaska Native
• Asian
• Black or African-American
• Hispanic or Latino Origin
• Hawaiian or Pacific Islander
• White
• Other
• More than 1 of the above

Neither the original study nor our replication found a statistically significant effect of race/ethnicity when the variable is dummy coded with White as the comparison group.  

Education

Participants could choose any of the following options for education:

• Did not complete high school
• High school diploma
• Some college
• Associate’s degree
• Four-year college degree
• Some graduate school
• Graduate school

We converted this to a numeric variable ranging from 0 (did not complete high school) to 6 (graduate school).

Neither the original study nor our replication found a statistically significant effect of education.

Interpreting the Results

All of the primary original-study results replicated in the data we collected, according to the replication criteria we pre-registered. 

It is worth highlighting that there was one minor statistical discrepancy between the primary results for the two datasets. The original study did not find statistical evidence for either a difference or equivalence between 20 years before birth and 40 years before birth. Our replication also found no statistical evidence for a difference between these timepoints, but it did find evidence for equivalence between the timepoints. We specified in advance that this pattern of results would qualify as a successful replication because it supports the original paper’s hypothesis that perceptions of moral decline diminish, disappear, or reverse when people are asked about time periods before they were born.

Among the secondary analyses, which tested the relationship between perceptions of moral decline and various demographic factors, our replication results differed from the original study results for a few variables. The original study found that only political ideology and age were statistically significant predictors of participants’ perceptions of moral decline. Our replication found similar results for political ideology, but it did not find age to be a significant predictor. Additionally, our replication found parental status and gender to be significant predictors. However, we strongly caution against interpreting the gender result strongly. This result was driven by the fact that the gender response option “Other” had a substantially different average moral decline rating from the response options “Male” and “Female,” but only 3 out of 533 participants comprised the “Other” category (see Figure 5). We consider this too small of a subgroup sample size to draw meaningful conclusions from. As we pre-registered, the secondary analyses were not considered in our replication ratings because they were not central to the paper’s hypotheses and the authors did not strongly interpret or theorize about the demographic-level findings.  

Finally, the paper was careful to note that its findings are not direct evidence for the biased exposure and biased memory effects that it postulates as causes of the perception of moral decline:

“The illusion of moral decline is a robust phenomenon that surely has several causes, and no one can say which of them produced the illusion that our studies have documented. Studies 5a and 5b do not directly implicate the BEAM mechanism in that production but they do make it a viable candidate for future research.” (p. 787)

We would like to reiterate this interpretation: the observed result is what one would expect if the biased exposure effect and biased memory effect gave rise to perceptions of moral decline, but this study does not provide causal evidence for either of these mechanisms.  

Conclusion

Overall, we successfully replicated all of the primary findings from the original study. Collectively, these findings suggest that people in the U.S. (aged 18-69), on average, perceive moral decline for time periods during their lifetimes, but not for time periods before they were born. The study received 5 stars for replicability.  

All of the study’s data, materials, and analysis code were publicly available and well-documented, which made this replication straightforward to conduct. We also successfully reproduced the results in the original paper using the provided data and analysis code. The one area for improvement on the transparency front is preregistration: this study was not pre-registered, even though it was very similar to a previous study in this paper (Study 2c). The study received 4.25 stars for transparency.

Generally, the study’s analyses were appropriate and its claims were well-calibrated to its study design and results. The study received 5 stars for clarity.

Acknowledgements

We want to thank the authors of the original paper for making their data, analysis code, and materials publicly available, and for their quick and helpful correspondence throughout the replication process. Any errors or issues that may remain in this replication effort are the responsibility of the Transparent Replications team.

We also owe a big thank you to our 533 research participants who made this study possible.

Finally, I am extremely grateful to Amanda Metskas and the rest of the Transparent Replications team for their advice and guidance throughout the project. 

Author Response

The authors of the original study shared the following response to this report:

“We are pleased to see these effects replicate, and we are grateful to the Transparent Replications team for their work.”

Dr. Adam Mastroianni via email 7/5/2024

Purpose of Transparent Replications by Clearer Thinking

Transparent Replications conducts replications and evaluates the transparency of randomly-selected, recently-published psychology papers in prestigious journals, with the overall aim of rewarding best practices and shifting incentives in social science toward more replicable research.

We welcome reader feedback on this report, and input on this project overall.

Appendices

Additional Information about the Methods

Recruitment

Both the original study and our replication recruited a sample of participants stratified by age. However, the original study and our replication used slightly different methods for doing so, which resulted in small differences in age-group proportions between the two studies. 

In the original study, participants were first asked to report their age. A quota system was set up inside the survey software such that, in theory, only 50 participants from each of the following age group should be allowed to participate: 18–24, 25–29, 30–34, 35–39, 40–44, 45–49, 50–54, 55–59, 60–64, 65–69. If participants indicated that they were 70 or older or if they were not among the first 50 participants from a given age group to take the study, they were not allowed to participate in the study (the original study did not have a perfect split by age, but it was quite close to 50 per group; see the table below). After completing the age question, participants completed the three English proficiency and knowledge of US American culture questions. If they failed any of the proficiency questions, they were not allowed to participate in the study.

In order to ensure that all participants were paid for the time they spent on the study, we did not use the same pre-screening process used in the original study. In the original study, if the age quota for a participant’s age group was already reached, or if a participant didn’t pass the screening questions, they were not paid for the initial screening questions they completed. In order to avoid asking participants to answer questions for which they wouldn’t be paid, we used age quotas within Positly to recruit participants in approximately equal proportions for each age group. Participants still indicated their age in the first part of the survey, but they were no longer screened out by a built-in age quota. This process did not achieve perfectly equal recruitment numbers by age group. We expect that this is because some participants reported an age in our experiment that differed from their listed age in the recruitment platform’s records. This could be for a variety of reasons including that some members of a household might share an account. 

Although our recruitment strategy did not achieve perfect stratification by age group, the two studies had relatively similar age-group breakdowns. The table below shows the pre-exclusion and post-exclusion stratification by age group for both studies.

We also want to note a minor deviation from our pre-registered recruitment strategy. In our pre-registration we said: 

“We will have 600 participants complete the study. If we do not have 520 or more participants remaining after we apply the exclusion criteria, then we will collect additional participants in batches of 20 until we reach 520 post-exclusion participants. We will not conduct any analyses until data collection is complete. When collecting data, we will apply age-group quotas by collecting 60 participants from each of the following ten age groups: 18–24, 25–29, 30–34, 35–39, 40–44, 45–49, 50–54, 55–59, 60–64, 65–69. If we need to recruit additional participants, we will apply the age-group quotas in such a way as to seek balance between the age groups.”

Because recruiting participants from the youngest age group (18-24) and the oldest age group (65-69) turned out to be extremely slow, we decided not to “apply the age-group quotas in such a way as to seek balance between the age groups” when we recruited participants beyond the original 600. (Note: We did not look at the dependent variables in the data until we had fully finished data collection, so this small deviation from the preregistration was not influenced by the data itself.) 

It’s also worth noting that the total number of participants we recruited was not a multiple of 20 despite our stated recruitment approach. This was because each time one collects data from an online crowdsourcing platform like Positly it’s possible that a few additional participants will complete the study than the original recruitment target. For example, sometimes participants complete the study in the survey software but do not indicate to the crowdsourcing platform that they completed the study. Because we had many rounds of recruitment for this study, each round had the opportunity to collect slightly more participants than the targeted number. 

Age group	Before exclusions		After exclusions
	Original study (n=499)	Replication study (n=721)	Original study (n=387)	Replication study (n=533)
18-24	10.0%	7.9%	9.8%	7.5%
25–29	10.4%	11.2%	8.8%	10.7%
30–34	10.4%	12.1%	10.3%	12.0%
35–39	10.8%	12.6%	11.6%	13.3%
40–44	10.2%	9.8%	11.4%	10.1%
45–49	10.0%	9.7%	10.1%	9.6%
50–54	10.0%	9.4%	10.1%	10.5%
55–59	10.0%	9.7%	10.9%	9.4%
60–64	8.2%	8.8%	8.5%	9.4%
65–69	9.8%	7.8%	8.5%	7.5%
70+	0%	0.8%	0%	0%

We also want to note one change we made in how subjects were recruited during our data collection. In the early portion of our data collection the recruited subjects first completed a pre-screener that asked the three English proficiency and knowledge of US American culture questions and confirmed that they were within the eligible age range for the study. All participants were paid for the pre-screener, and those who passed it were invited to continue on to take the main study. 146 participants passed the pre-screener and went on to take the main study.

We found that the pre-screening process was slowing down recruitment, so we incorporated the screening questions into the main study and allowed recruited participants to complete and be paid for the study even if they failed the screening. We excluded participants who failed the screening from our data analysis. 575 participants took the study after this modification was made.

Finally, it’s important to note that our pre-exclusion sample size of n=721 is the number of participants who provided consent to participate in our study; the number of participants in our replication who passed the screening criteria of being between ages 18-69 and correctly answering the three English proficiency and knowledge of US American culture questions was n=703. 

Additional Information about the Results

Corrections for multiple comparisons

For the primary analysis in which participants’ morality ratings are compared between timepoints, we followed the analytical approach used in the original paper and used a Holm-Bonferroni correction for multiple comparisons for the four contrasts that were tested. However, we think it is unnecessary to correct for multiple comparisons in this situation. As argued by Rubin (2024), multiple comparisons would only be necessary in this context if the authors would have considered their hypothesis confirmed if at least one of the contrasts returned the hypothesized result. Rather, the authors needed each of the four contrasts to match their expected pattern in order to confirm their hypothesis. As such, we argue that correcting for multiple comparisons is overly conservative in this study. However, not correcting for multiple comparisons on our replication data does not change the statistical significance of any of the findings.

Region of practical equivalence (ROPE) for equivalence tests 

It’s important to note that when conducting equivalence tests, evidence for equivalence depends on what one sets as the region of practical equivalence (ROPE). The original authors chose to use the default calculation of ROPE in the parameters package in R (see here for more information). Given that the original study was not pre-registered, we think this is a reasonable decision; after knowing the study results, it could be difficult to justify a particular ROPE without being biased by how this would affect the findings. To make our results comparable to the original study, we also used the default calculation of ROPE. However, we want to note that this is not a theoretical justification for the specific ROPE used in this study; other researchers might reasonably argue for a wider or narrower ROPE. 

References

Faul, F., Erdfelder, E., Buchner, A., & Lang, A.-G. (2009). Statistical power analyses using G*Power 3.1: Tests for correlation and regression analyses. Behavior Research Methods, 41, 1149-1160. Download PDF

Mastrioanni, A. M., & Gilbert, D. T. (2023). The illusion of moral decline. Nature, 618, 782–789. https://doi.org/10.1038/s41586-023-06137-x 

Rubin, M. (2024). Inconsistent multiple testing corrections: The fallacy of using family-based error rates to make inferences about individual hypotheses. Methods in Psychology, 10, 100140. https://doi.org/10.1016/j.metip.2024.100140

Executive Summary

Transparency	Replicability	Clarity
	1 of 1 findings replicated

We ran a replication of Study 2 from this paper, which found that participants place greater value on information in situations where they’ve been specifically assigned or “endowed with” that information compared to when they are not endowed with that information. This is the case even if that information is not of any particular use (i.e., people exhibit the endowment effect for noninstrumental information). This finding was replicated in our study.

The original study randomized participants into two conditions: endowed and nonendowed. In the endowed condition, participants were told that they were on course to learn a specific bundle of three facts and were then offered the option to learn a separate bundle of four facts instead. In the nonendowed condition, participants were simply offered a choice between learning a bundle of three or a separate bundle of four facts, with the bundles shown in randomized order. Results of a chi-square goodness-of-fit test indicated that participants in the endowed condition were more likely to express a preference for learning three (versus four) facts than participants in the nonendowed condition. This supported the original researchers’ hypothesis that individuals exhibit the endowment effect for non-instrumental information.  This finding was replicated in our study.

We simultaneously ran a second experiment to investigate the possibility that order effects could have contributed to the results of the original study. Our second experiment found that (even when controlling for order effects) there was still evidence of the endowment effect for noninstrumental information.

The original study (Study 2) received a replicability rating of five stars as its findings replicated in our replication analysis. It received a transparency rating of 4.25 stars. The methods, data, and analysis code were publicly available. Study 2 (unlike the others in the paper) was not pre-registered. The study received a clarity rating of 3 stars as its methods, results, and discussion were presented clearly and the claims made were well-supported by the evidence provided; however, the randomization and the implications of choice order for participants in the nonendowed condition was not clearly described in the study materials. Although randomization was mentioned in the supplemental materials, the implications of this randomization and the way that it could influence the interpretation of results were not explored in either the paper or supplemental materials.

Full Report

Study Diagram

Replication Conducted

We ran a replication of Study 2 from: Litovsky, Y., Loewenstein, G., Horn, S., & Olivola, C. Y. (2022). Loss aversion, the endowment effect, and gain-loss framing shape preferences for noninstrumental information. Proceedings of the National Academy of Sciences, 119(34). https://doi.org/10.1073/pnas.2202700119

How to cite this replication report: Transparent Replications by Clearer Thinking. (2024). Report #9: Replication of a study from “Loss Aversion, the Endowment Effect, and Gain-Loss Framing Shape Preferences for Noninstrumental Information” (PNAS | Litovsky et al., 2022) https://replications.clearerthinking.org/replication-2022pnas119-34
(Preprint DOI: https://doi.org/10.31234/osf.io/efa73)

Key Links

• Our Research Box for this replication report includes the pre-registration, study materials, de-identified data, and analysis files.
• You can read the original paper here.
• Here, you can review the supplemental materials and the data and experimental stimuli for the original paper.

Overall Ratings

To what degree was the original study transparent, replicable, and clear?

Transparency:  how transparent was the original study?	The methods, data, and analysis code were publicly available. The study (unlike the others in the paper) was not pre-registered.
Replicability: to what extent were we able to replicate the findings of the original study?	The original finding replicated.
Clarity: how unlikely is it that the study will be misinterpreted?	Methods, results, and discussion were presented clearly and all claims were well-supported by the evidence provided; however, the paper did not control for order effects or discuss the implications of choice order for participants in the nonendowed condition.

Detailed Transparency Ratings

Overall Transparency Rating:
1. Methods Transparency:	The materials are publicly available and complete.
2. Analysis Transparency:	The analyses were described clearly and accurately.
3. Data availability:	The cleaned data was publicly available; the deidentified raw data was not publicly available.
4. Preregistration:	Study 2 (unlike the others in the paper) was not pre-registered.

Summary of Original Study and Results

The endowment effect describes “an asymmetry in preferences for acquiring versus giving up objects” (Litovsky, Loewenstein, Horn & Olivola, 2022). Building off seminal work from Daniel Kahneman and other scholars (e.g. 1991; 2013), Litovsky and colleagues found that the endowment effect impacts preferences for “owning” noninstrumental information.

Results of a chi-square goodness-of-fit test in the original study indicated that participants in the endowed condition (each of whom was “endowed” with a 3-fact bundle) were more likely to express a preference for learning three (as opposed to four) facts (68%) than participants in the nonendowed condition (46%) (χ2(1, n = 146) = 7.03, P = 0.008, Φ = 0.219). This led the researchers to confirm their hypothesis that individuals exhibit the endowment effect for noninstrumental information.

Study and Results in Detail

Methods

In the original study, participants were randomly assigned to one of two conditions: endowed or nonendowed. Illustrations of these conditions are shown below in Figures 1 and 2. In the endowed condition, participants were told that they were on course to learn a specific bundle of three facts and were then offered the option to learn a different bundle of four facts instead. In the nonendowed condition, participants were shown two options that they could freely choose between: the 3-fact bundle and the 4-fact one. The choice order was randomized, so the 3-fact bundle was on top half the time and the 4-fact bundle was on top the other half of the time.

None of the facts presented were of objectively greater utility or interest than any of the others. Facts related to, for example, the behavior of a particular animal, or the fact that the unicorn is the national animal of a country. Furthermore, each time they ran the experiment, they randomized which facts appeared in which order across both bundles. The subjective utility of a given fact would not be expected to affect experimental results due to this randomization process.

Figure 1: Endowed Condition

Figure 2: Nonendowed Conditions

In the original experiment, two variables had varied across conditions – both endowment and the order of presentation of the two bundles had varied. Option order had been randomized within the nonendowed condition such that a 3-fact bundle was shown on top half the time while a 4-fact bundle was shown on top the other half of the time within that condition. On the other hand, option order was not randomized in the endowed condition: the 3-fact  bundle always shown on top within that condition. To control for ordering effects, we increased sample size to 1.5 times our original planned size and split the nonendowed condition (now double the size it would otherwise have been) into two separate conditions: Conditions 2 and 3. 

Our participants were randomized into one of three conditions, as described below:

• Condition 1: Endowed – Participants were told that they were on course to learn a specific bundle of three facts and were then offered the option to learn four different facts instead.
• Condition 2: Nonendowed with 3-fact bundle displayed on top – Participants were offered a choice between learning three facts or four facts, with the bundle of 3 facts appearing as the top option.
• Condition 3: Nonendowed with 4-fact bundle displayed on top – Participants were offered a choice between learning three facts or four facts, with the bundle of 4 facts appearing as the top option

When Conditions 2 and 3 are pooled together, they are equivalent to the original study’s single nonendowed condition, which presented the 3- and 4-fact bundles in randomized order. In keeping with the original experiment, we compared the key outcome variable, preference for learning three (rather than four) facts, in the endowed condition and the combined nonendowed condition (the latter being the pooled data from Conditions 2 and 3, which together are equivalent to the original experiment’s nonendowed condition). However, we also considered an additional comparison not made in the original study: the proportion choosing the 3-fact bundle in Condition 1 versus Condition 2 alone.  

The original study included 146 adult participants from Prolific. Our replication included 609 adult participants (after 22 were excluded from the 631 who finished it) from MTurk via Positly.com.

Data and Analysis

Data Collection

Data were collected using the Positly platform over a two-week period in February and March, 2024. To follow the original study, in order to detect an effect size as low as 75% of the original effect size with 90% power, a sample size of 391 would be required; however, in order to complete the additional analysis, we doubled the number of participants in the nonendowed condition (before then dividing the original single nonendowed condition into two conditions). This required data to be collected from at least 578 participants, after accounting for excluded participants, as described below.

Excluding Observations

Any responses for which there were missing data were not included in our analyses. We also excluded participants who reported that they had completed a similar study on Prolific in the past (N = 22). The latter point was assessed via the final question in the experiment, “Have you done this study (or one very similar to it) on Prolific in the past?” Answer options include: (1) Yes, I have definitely done this study (or one very similar to it) on Prolific before; (2) I think I’ve done this study (or one very similar to it) on Prolific before, though I’m not sure; (3) I don’t think I’ve done this study (or one very similar to it) on Prolific before, though I’m not sure; and (4) No, I definitely haven’t done this study or anything like it before. Our main analysis included all participants who selected options 3 or 4 (total N = 609). Our (pre-planned) supplementary analyses only included participants who had selected option 4 (N = 578).

Analysis

To evaluate the replicability of the original study, we ran a chi-square goodness-of-fit test to evaluate differences in preference for learning three facts between participants in the endowed versus the pooled nonendowed conditions. As stated in the pre-registration, our policy was to consider the study to have replicated if this test yielded a statistically significant result, with the difference in the same direction as the original finding (i.e., with a higher proportion of participants selecting the 3-fact bundle in the endowed compared to the pooled nonendowed conditions).

Results

Main Analyses

As per our pre-registration, our main analysis included all participants who completed the study and who reported that they believed that they had not completed this study, or one similar to it, in the past. We found that participants in the endowed condition selected the 3-fact bundle more frequently than participants in the nonendowed condition (71% vs. 44%, respectively) (χ² (1, n = 609) = 40.122, p < 0.001).

We also conducted another analysis to evaluate the design features of the original study using these same inclusion criteria. Using a chi-square goodness-of-fit test, we compared the proportion choosing the 3-fact bundle in Condition 1 versus Condition 2 alone, finding again that the proportion of participants choosing the 3-fact bundle in Condition 1 (71%) to be significantly greater than the proportion of participants choosing the 3-fact bundle in Condition 2 (43%) (χ² (1, n = 410) = 33.596, p < 0.001). 

Supplementary Analyses

Using only those participants who reported that they definitely had not completed this study (or one similar to it) in the past, we again found that participants in the endowed condition selected the 3-fact bundle more frequently than participants in the nonendowed condition (71% vs. 43%, respectively) (χ² (1, n = 578) = 39.625, p < 0.001, Φ = 0.26) and that the proportion of participants choosing the 3-fact bundle in Condition 1 (71%) was significantly greater than the proportion of participants choosing the 3-fact bundle in Condition 2 (42%) (χ² (1, n = 391) = 31.716, p < 0.001, Φ = 0.285). 

Interpreting the Results

The label “noninstrumental information” was used in this report to follow the language present in the original study. It should be noted, however, that some individuals might consider discovering new and potentially fun or interesting information to carry some instrumental value as it enables them to act on curiosity, learn something new, amuse themselves, or possibly share novel information with others.

We note that the proportion of participants who chose 3 facts in the nonendowed condition closely mirrored the proportion of the total facts represented by 3 (i.e. 3/7 = 43%). This is consistent with an interpretation that people might be drawn to what they believe to be the single most interesting fact and might make their choice (in the nonendowed condition, at least) based on which bundle contains the fact they perceive to be most interesting. 

Conclusion

We replicated the original study results and confirmed they held when controlling for an alternative explanation we’d identified. Participants displayed the endowment effect for noninstrumental information based on their preference for choosing to learn a random 3-fact bundle that they had been endowed with, rather than a 4-fact bundle presented as an alternative option. The original study received a replicability rating of five stars as its findings replicated in all replication analyses. It received a transparency rating of four stars due to the public availability of the methods, data, and analysis code but also the lack of a preregistration. The study received a clarity rating of 3 stars as its methods, results, and discussion were presented clearly and the claims made were well-supported by the evidence provided; however, the randomization and the implications of choice order for participants in the nonendowed condition was not clearly described in the paper or study materials. 

Acknowledgements

We would like to acknowledge the authors of the original paper. Their experimental materials and data were shared transparently, and their team was very communicative and cooperative. In particular, we thank them for their thoughtful feedback on our materials over several review rounds. 

We would also like to acknowledge the late Daniel Kahneman, a motivating force behind the original study. We acknowledge his many contributions to the fields of psychology and behavioral economics.

We would like to thank the Transparent Replications team, especially Amanda Metskas and Spencer Greenberg for their support through this process, including their feedback on our idea to add an extension arm to the study to control for the order effects we had identified as a potential alternative (or contributing/confounding) explanation for the original study’s findings. We are very grateful to our Independent Ethics Evaluator, who made an astute observation regarding our early sample size planning (in light of our additional study arm having been introduced after our initial power analysis) that resulted in us reviewing and improving our plans for the extension arm of the study. Last but not least, we are grateful to all the study participants for their time and attention. 

Purpose of Transparent Replications by Clearer Thinking

Transparent Replications conducts replications and evaluates the transparency of randomly-selected, recently-published psychology papers in prestigious journals, with the overall aim of rewarding best practices and shifting incentives in social science toward more replicable research.

We welcome reader feedback on this report, and input on this project overall.

References

Faul, F., Erdfelder, E., Buchner, A., & Lang, A.-G. (2009). Statistical power analyses using G*Power 3.1: Tests for correlation and regression analyses. Behavior Research Methods, 41, 1149-1160. Download PDF

Kahneman, D., Knetsch, J. L., & Thaler, R. H. (1990). Experimental tests of the endowment effect and the Coase theorem. Journal of Political Economy, 98(6), 1325-1348

Kahneman, D., Knetsch, J. L., & Thaler, R. H. (1991). Anomalies: The endowment effect, loss aversion, and status quo bias. Journal of Economic Perspectives, 5, 193–206.

Litovsky, Y., Loewenstein, G., Horn, S., & Olivola, C. Y. (2022). Loss aversion, the endowment effect, and gain-loss framing shape preferences for noninstrumental information. Proceedings of the National Academy of Sciences, 119(34). https://doi.org/10.1073/pnas.2202700119

Transparent Replications presented our project and preliminary results at the Year of Open Science Culminating Conference. This virtual conference was a collaboration between the Open Science Foundation and NASA and was attended by over 1,000 people. Now you can see our presentation too!

The Transparent Replications presentation is the first fifteen minutes of this video. After our presentation the session continues with two more organizations presenting their work followed by a brief Q&A.

We really appreciated the opportunity to share what we are working on. If you have any feedback for us, or want to get involved, please don’t hesitate to contact us!

Executive Summary

Transparency	Replicability	Clarity
	10 of 10 findings replicated

We ran a replication of Study 1 from this paper, which tested whether a series of popular logos and characters (e.g., Apple logo, Bluetooth symbol, Mr. Monopoly) showed a “Visual Mandela Effect”—a phenomenon where people hold “specific and consistent visual false memories for certain images in popular culture.” For example, many people on the internet remember Mr. Monopoly as having a monocle when, in fact, the character has never had a monocle. The original study found that 7 of the 40 images it tested showed evidence of a Visual Mandela Effect: C-3PO, Fruit of the Loom logo, Curious George, Mr. Monopoly, Pikachu, Volkswagen logo, and Waldo (from Where’s Waldo). These results fully replicated in our study. 

In the study, participants evaluated one popular logo or character image at a time. For each image, participants saw three different versions. One of these versions was the original, while the other two versions had subtle differences, such as a missing feature, an added feature, or a change in color. Participants were asked to select which of these three versions was the correct version. Participants then rated how confident they felt in their choice, how familiar they were with the image, and how many times they had seen the image before.

If people chose one particular incorrect version of an image statistically significantly more often than they chose the correct version of an image, that was considered evidence of a possible Visual Mandela Effect for that image.

The study received a transparency rating of 3.5 stars because its materials and data were publicly available, but it was not pre-registered and there were insufficient details about some of its analyses. The paper received a replicability rating of 5 stars because all of its primary findings replicated. The study received a clarity rating of 2.5 stars due to errors and misinterpretations in some of the original analyses.

Full Report

Study Diagram

Replication Conducted

We ran a replication of Study 1 from: Prasad, D., & Bainbridge, W. A. (2022). The Visual Mandela Effect as Evidence for Shared and Specific False Memories Across People. Psychological Science, 33(12), 1971–1988. https://doi.org/10.1177/09567976221108944

How to cite this replication report: Transparent Replications by Clearer Thinking. (2024). Report #8: Replication of a study from “The Visual Mandela Effect as Evidence for Shared and Specific False Memories Across People” (Psychological Science | Prasad & Bainbridge 2022) https://replications.clearerthinking.org/replication-2022psci33-12
(Preprint DOI: https://doi.org/10.31234/osf.io/3pejm)

Key Links

• Our Research Box for this replication report includes the pre-registration, study materials, de-identified data, and analysis files.
• Download a PDF of the preprint version of the original paper
• Review the supplemental materials and the data and experimental stimuli for the original paper.

Overall Ratings

To what degree was the original study transparent, replicable, and clear?

Transparency: how transparent was the original study?	Study materials and data are publicly available. The study was not pre-registered. Analysis code is not publicly available and some analyses were described in insufficient detail to reproduce.
Replicability: to what extent were we able to replicate the findings of the original study?	All of the study’s main findings replicated.
Clarity: how unlikely is it that the study will be misinterpreted?	The analyses, results, and interpretations are stated clearly. However, there is an error in one of the primary analyses and a misinterpretation of another primary analysis. First, the χ2 test was conducted incorrectly. Second, the split-half consistency analysis does not seem to add reliably diagnostic information to the assessment of whether images show a VME (as we demonstrate with simulated data). That said, correcting for these errors and misinterpretations with the original study’s data results in similar conclusions for 6 out of the 7 images identified in the original study as showing the Visual Mandela Effect. The seventh image dropped below significance when the corrected analysis was run on the original data; however, we evaluated that image as part of the replication since it was claimed as a finding in the paper, and we found a significant result in our replication dataset.

Detailed Transparency Ratings

Overall Transparency Rating:
1. Methods Transparency:	The materials are publicly available and complete.
2. Analysis Transparency:	The analysis code is not publicly available. Some of the analyses (the χ2 test and the Wilcoxon Rank-Sum Test) were described in insufficient detail to easily reproduce the results reported in the paper. The paper would benefit from publicly available analysis code and supplemental materials that describe the analyses and results in greater detail.
3. Data availability:	The cleaned data was publicly available; the deidentified raw data was not publicly available.
4. Preregistration:	Study 1 was not pre-registered; however, it was transparently described as an exploratory analysis.

Summary of Study and Results

The original study (N=100) and our replication (N=389) tested whether a series of 40 popular logo and character images show evidence of a Visual Mandela Effect (VME). The Mandela Effect is a false memory shared by a large number of people. The name of the effect refers to an instance of this phenomenon where many people remember Nelson Mandela dying in prison during the Apartheid regime in South Africa, despite this not being the case. This article examines a similar effect occurring for specific images. The authors specified five criteria that images would need to meet in order to show a VME: 

(a) the image must have low identification accuracy 
(b) there must be a specific incorrect version of the image falsely recognized 
(c) these incorrect responses have to be highly consistent across people 
(d) the image shows low accuracy even when it is rated as being familiar
(e) the responses on the image are given with high confidence even though they are incorrect

(Prasad & Bainbridge, 2022, p. 1974)

To test for VME images, participants saw three versions of each image concept. One version was the correct version. The other two versions were altered using one of five possible manipulations: adding a feature; subtracting a feature; changing a feature; adjusting the position or orientation of a feature; changing the color of a feature. For example, for the Mr. Monopoly image, one altered version added a monocle over one eye and the other altered version added glasses.

For each image, participants did the following:

• Chose the version of the image they believed to be the correct (i.e., canonical) version 
• Rated how confident they felt in their choice (1 = not at all confident; 5 = extremely confident)
• Rated how familiar they were with the image (1 = not at all familiar; 5 = extremely familiar) 
• Rated how many times they had seen the image before (0; 1-10; 11-50; 51-100; 101-1000; 1000+)

Figure 1 shows what this process looked like for participants, using the Mr. Monopoly image as an example.

Assessing criteria (a) and (b)

Following the general approach used in the original paper, we tested whether each of the 40 images met criteria (a) and (b) by assessing whether one version of the image was chosen more commonly than the other versions. If one incorrect version was chosen more often than both the correct version and the other incorrect version, this was considered evidence of low identification accuracy and evidence that a specific incorrect version of the image was falsely recognized. The original study identified 7 images meeting criteria (a) and (b). Upon reproducing these results with the original data, we noticed an error in the original analysis (see Study and Results in Detail and the Appendix for more information). When we corrected this error, 6 images in the original data met these criteria. In the new data we collected for our replication, 8 images met these criteria, including the 7 identified in the original paper.

Table 1. Original and replication results for VME criteria (a) and (b)

Test of criteria (a) and (b): For each image, is a specific, incorrect version chosen more frequently than the correct version?	Original result	Replication result
C-3P0	+	+
Curious George	+	+
Fruit of the Loom Logo	+	+
Mr. Monopoly	+	+
Pikachu	+	+
Tom (Tom & Jerry)	0	+
Volkswagen Logo	+	+
Waldo (Where’s Waldo?)	+*	+
The other 32 images	–	–

Assessing criterion (c)

We did not run a separate analysis to test whether each image met criterion (c). After conducting simulations of the split-half consistency analysis used in the original study to assess criterion (c), we concluded that this analysis does not contribute any additional reliable information to test whether incorrect responses are highly consistent across people beyond what is already present in the histogram of the data. Moreover, we argue that if an image meets criteria (a) and (b), it should also meet (c). (See Study and Results in Detail and the Appendix for more information.)

Assessing criteria (d) and (e)

Following the general approach used in the original paper, we tested whether each image met criteria (d) and (e) by running a series of permutation tests to assess the strength of three different correlations when a set of images was excluded from the data. Specifically, we tested whether the following three correlations were stronger when the 8 images that met criteria (a) and (b) were excluded compared to when other random sets of 8 images were excluded:

• The correlation between familiarity and confidence
• The correlation between familiarity and accuracy
• The correlation between confidence and accuracy

In line with the authors’ expectations, there was no evidence in either the original data or in our replication data that the correlation between familiarity and confidence changed when the VME-apparent images were excluded compared to excluding other images. By contrast, when examining correlations with accuracy, there was evidence that excluding the VME-apparent images strengthened correlations compared to excluding other images.

The original study found that the positive correlation between familiarity and accuracy was higher when the specific images that met criteria (a) and (b) were excluded, suggesting that those images did not have the strong positive relationship between familiarity and accuracy observed among the other images. Similarly, the original study also found that the positive correlation between confidence and accuracy was higher when the specific images that met criteria (a) and (b) were excluded, suggesting that those images did not have the strong positive relationship between confidence and accuracy observed among the other images. In our replication data, we found the same pattern of results for these correlations.

Table 2. Original and replication results for VME criteria (d) and (e)

Test of criteria (d) and (e): Is the correlation of interest higher when the images that meet criteria (a) and (b) are dropped from the sample?	Original result	Replication result
Correlation between confidence and familiarity	0	0
Correlation between familiarity and accuracy	+	+
Correlation between confidence and accuracy	+	+

Study and Results in Detail

This section goes into greater technical detail about the analyses and results used to assess the five Visual Mandela Effect (VME) criteria the authors specified:

(a) the image must have low identification accuracy 
(b) there must be a specific incorrect version of the image falsely recognized 
(c) these incorrect responses have to be highly consistent across people
(d) the image shows low accuracy even when it is rated as being familiar
(e) the responses on the image are given with high confidence even though they are incorrect

(Prasad & Bainbridge, 2022, p. 1974)

Evaluating images on criteria (a) and (b)

To assess whether each of the 40 images met VME-criteria (a) and (b), we first calculated the proportion of participants who chose each of the three image versions (see Figure 2). Image choices were labeled as follows:

• “Correct” = the canonical version of the image
• “Manipulation 1” = the more commonly chosen version of the two non-canonical versions
• “Manipulation 2” = the less commonly chosen version of the two non-canonical versions

We then ran a χ² goodness-of-fit test to assess whether, for each image, the Manipulation 1 version was chosen statistically significantly more often than the Correct version. The test revealed that, for 8 of the 40 images, the Manipulation 1 version was chosen statistically significantly more often than the Correct version.

There were no images for which the Manipulation 2 version was chosen more often than the Correct version, so we did not need to formally test whether the Manipulation 1 version was also chosen more often than the Manipulation 2 version for these 8 images. All 7 of the images identified in the original paper as meeting criteria (a) and (b) were among the 8 images we identified (See table 1). 

It is important to note that, in the original study, this analysis was conducted using a χ² test of independence rather than a χ² goodness-of-fit test. However, using a χ² test of independence in this situation violates one of the core assumptions of the χ² test of independence—that the observations are independent. Because participants could only choose one option for each image concept, whether a participant chose the Manipulation 1 image was necessarily dependent on whether they chose the correct image. The way the χ² test of independence was run in the original study led to an incorrect inflation of the χ² values. Thus, per our pre-registration, we ran a χ² goodness-of-fit test (rather than a χ² test of independence) to assess whether a specific incorrect version of each image was falsely identified as the correct version. For a more thorough explanation of the issues with the original analytical technique, see the Appendix.

In the original study, which used the χ² test of independence, 7 of the 40 images were classified as meeting criteria (a) and (b). When we reanalyzed the original data using a χ² goodness-of-fit test, 1 of those 7 images (Waldo from Where’s Waldo) was no longer statistically significant. In our replication data, all 7 of these images (including Waldo) were statistically significant, as was 1 additional image (Tom from Tom & Jerry). Table 3 summarizes these findings.

Table 3. Reported, reproduced, and replicated results for criteria (a) and (b) for each of the images found to be VME-apparent

Image	Reported results*:	Reproduced results:	Replicated results:
	χ2 test of independence (incorrect statistical test) on original data	χ2 goodness-of-fit test (correct statistical test)on original data	χ2 goodness-of-fit test (correct statistical test)on replication data
C-3PO	χ2 (1, N=194) = 62.61,  p = 2.519e-15	χ2 (1, N=91) = 33.24,  p = 8.138e-09	χ2 (1, N=359) = 99.50,  p = 1.960e-23
Curious George	χ2 (1, N=194) = 45.62,  p = 1.433e-11	χ2 (1, N=93) = 23.75,  p = 1.095e-06	χ2 (1, N=384) = 70.04,  p = 5.806e-17
Fruit of the Loom Logo	χ2 (1, N=190) = 6.95,  p = 0.008	χ2 (1, N=82) = 3.95,  p = 0.047	χ2 (1, N=369) = 10.08,  p = 0.001
Mr. Monopoly	χ2 (1, N=196) = 20.08,  p = 7.416e-06	χ2 (1, N=83) = 11.58,  p = 6.673e-04	χ2 (1, N=378) = 4.67,  p = 0.031
Pikachu	χ2 (1, N=194) = 12.46,  p = 4.157e-04	χ2 (1, N=76) = 7.58,  p = 0.006	χ2 (1, N=304) = 39.80,  p = 2.810e-10
Tom (Tom & Jerry)	χ2 (1, N=194) = 2.51,  p = 0.113	χ2 (1, N=89) = 1.36,  p = 0.244	χ2 (1, N=367) = 23.57,  p = 1.207e-06
Volkswagen Logo	χ2 (1, N=198) = 30.93,  p = 2.676e-08	χ2 (1, N=91) = 16.71,  p = 4.345e-05	χ2 (1, N=362) = 54.14,  p = 1.864e-13
Waldo (Where’s Waldo?)	χ2 (1, N=196) = 6.71,  p = 0.010	χ2 (1, N=86) = 3.77,  p = 0.052	χ2 (1, N=351) = 26.81,  p = 2.249e-07

Evaluating images on criterion (c)

To evaluate images on the VME-criterion of “(c) these incorrect responses have to be highly consistent across people,” the original study employed a split-half consistency analysis. After running simulations with this analysis, we concluded that the analytical technique employed in the original study does not contribute reliable information towards evaluating this criteria beyond what is already shown in the histogram of the data. You can see a detailed explanation of this in the Appendix.  

Additionally, whether an image meets criterion (c) is, arguably, already assessed in the tests used to evaluate criteria (a) and (b). When discussing criterion (c), the authors state, “VME is also defined by its consistency; it is a shared specific false memory” (p. 1974). If an image already meets criterion (a) by having low identification accuracy and criterion (b) by having a specific incorrect version of the image be falsely recognized as the canonical version, that seems like evidence of a specific false memory that is consistent across people. This is because in order for some images in the study to meet both of those criteria, a large percentage of the participants would need to select the same incorrect response as each other for those images.

As such, we did not pre-register an analysis to assess criterion (c), and the split-half consistency analysis is not considered in our replication rating for this study.

Evaluating images on criteria (d) and (e)

To evaluate images on the VME-criteria of “(d) the image shows low accuracy even when it is rated as being familiar” and “(e) the responses on the image are given with high confidence even though they are incorrect,” the original study used a series of permutation tests to assess the relationships between accuracy (i.e., the proportion of people who chose the correct image), familiarity ratings, and confidence ratings. 

Here’s how the permutation tests worked in the original study, using the permutation test assessing the correlation between confidence ratings and familiarity ratings as an example:

1. 7 images were selected at random and dropped from the dataset (this number corresponds to the number of images identified as meeting criteria (a) & (b))
2. For the remaining 33 images, the average confidence rating and average familiarity rating of each image were correlated
3. Steps 1-2 were repeated for a total of 1,000 permutations 
4. The specific 7 images that met criteria (a) and (b) were dropped from the dataset (C-3PO, Fruit of the Loom Logo, Curious George, Mr. Monopoly, Pikachu, Volkswagen Logo, Waldo)
5. The average confidence rating and average familiarity rating of each of the 33 remaining images were correlated for this specific permutation
6. The correlation calculated in Step 5 was compared to the 1,000 correlations calculated in Steps 1-3

The original study used the same permutation test two more times to assess the correlation between average confidence ratings and accuracy and the correlation between average familiarity ratings and accuracy.

The original study found that the correlation between confidence and accuracy and the correlation between familiarity and accuracy were both higher when the 7 specific images that met criteria (a) and (b) were dropped. Additionally, in line with the authors’ predictions for VME images, the original study did not find evidence that the correlation between familiarity and confidence was different when the 7 specific images were dropped. 

As noted earlier, when the correct analysis (χ² goodness-of-fit test) is used to evaluate criteria (a) and (b) on the original data, there is no longer statistically significant evidence that Waldo meets criteria (a) and (b). As such, we re-ran these three permutation tests on the original data, but only dropped the 6 images that met criteria (a) and (b) when using the correct analysis (C-3PO, Fruit of the Loom Logo, Curious George, Mr. Monopoly, Pikachu, Volkswagen Logo). We find similar results to when the 7 images were dropped. See the appendix for the specific findings from this re-analysis. 

With our replication data, we conducted the same three permutation tests, with a few minor differences:

• We ran 10,000 permutations (without replacement) rather than 1,000. The additional permutations give the test greater precision.
• We dropped 8 images (C-3PO, Fruit of the Loom Logo, Curious George, Mr. Monopoly, Pikachu, Tom, Volkswagen Logo, Waldo), which correspond to the images that met criteria (a) and (b) in our replication data. 

We found the same pattern of results as the reported results. 

Table 4. Reported results and replicated results for criteria (d) and (e)

Permutation test	Reported results (1,000 permutations): Dropping 7 images: C-3PO, Fruit of the Loom Logo, Curious George, Mr. Monopoly, Pikachu, Volkswagen Logo, Waldo (Where’s Waldo)	Replicated results (10,000 permutations): Dropping 8 images: C-3PO, Fruit of the Loom Logo, Curious George, Mr. Monopoly, Pikachu, Tom (Tom & Jerry), Volkswagen Logo, Waldo (Where’s Waldo)
Correlation between confidence and familiarity	p = 0.540	p = 0.320
Correlation between familiarity and accuracy	p = 0.044	p = 0.003
Correlation between confidence and accuracy	p = 0.001	p = 0.000

Interpreting the Results

All of the primary findings from the original study that we attempted to replicate did indeed replicate. 

Interestingly, even the reported finding that Waldo (from Where’s Waldo) showed evidence of a VME replicated, despite the fact that this claim was based on an incorrect analysis in the original paper. It is worth noting that, even though there is not statistically significant evidence that Waldo shows a VME when the correct analysis is performed on the original data, the raw proportions of which versions of Waldo were chosen are directionally consistent with a VME. In other words, even in the original data, more people chose a specific, incorrect version of the image than chose the correct version (but not enough for it to be statistically significant). This, coupled with the fact that we find a statistically significant result for Waldo in the replication data, suggests that the original study did not have enough statistical power to detect this effect. 

A similar thing likely happened with Tom (Tom & Jerry). There was not statistically significant evidence that Tom showed a VME in the original data. Nevertheless, even in the original data, more people chose a specific, incorrect version of Tom than chose the correct version. In our replication data, we found statistically significant evidence that Tom showed a VME. 

So, even though Waldo and Tom were not statistically significant when using the correct analysis on the original data, but were statistically significant in our replication data, we do not view this as a major discrepancy between the findings in the two studies.

We would also like to note one important limitation of the permutation tests. The way these tests were conducted in the original paper, the correlations between confidence, familiarity, and accuracy were conducted on the average values of confidence, familiarity, and accuracy for each image. Averaging at the image level can obscure important individual-level patterns. Thus, we argue that a better version of this analysis would be to correlate these variables across each individual data point, rather than across the average values for each image. That said, when we ran the individual-level version of this analysis on both the original data and our replication data, we found that the results were all directionally consistent with the results of this test conducted on the image-level averages. See the Appendix for a more thorough explanation of the limitation of using image-level averages and to see the results when using an individual-level analytical approach.   

Finally, it’s worth noting that the original paper reports one more analysis that we have not discussed yet in this report. The original study reports a Wilcoxon Rank Sum test to assess whether there was a difference in the number of times participants had seen the images that met the VME criteria versus the images that did not meet the VME criteria. The original paper reports a null result (z = 0.64, p = 0.523). We were unable to reproduce this result using the original data. We ran this test in seven different ways, including trying both Wilcoxon Rank Sum tests (which assume independent samples) and Wilcoxon Signed Rank tests (which assume paired samples) and running the test without aggregating the data and with aggregating the data in various ways. (See the Appendix for the full description and results for these analyses.) It is possible that none of these seven ways of running the test matched how the test was run in the original study. Without access to the original analysis code, we cannot be sure why we get different results. However, because this test was not critical to any of the five VME criteria, we did not pre-register and run this analysis for our replication study. Moreover, our inability to reproduce the result did not influence the study’s replicability rating.   

Conclusion

The original paper specifies five criteria (a-e) that images should meet in order to show evidence of a Visual Mandela Effect (VME). Based on these five criteria, the original paper reports that 7 out of the 40 images they tested show a VME.  

When we attempted to reproduce the paper’s results using the original data, we noticed an error in the analysis used to assess criteria (a) and (b). When we corrected this error, only 6 of the 40 images met the VME criteria. Additionally, we argued that the analysis for criterion (c) was misinterpreted, and should not serve as evidence for criterion (c). However, we also argued that criterion (c) was sufficiently tested by the analyses used to test criteria (a) and (b), and thus did not require its own analysis. 

As such, with our replication data, we ran similar analyses to those run in the original paper to test criteria (a), (b), (d), and (e), with the error in the criteria (a) and (b) analysis fixed. In our replication data, we found that 8 images, including the 7 claimed in the original paper, show a VME. Thus, despite the analysis errors we uncovered in the original study, we successfully replicated the primary findings from Study 1 of Prasad & Bainbridge (2022).

The study received a replicability rating of 5 stars, a transparency rating of 3.5 stars, and a clarity rating of 2.5 stars.

Acknowledgements

We want to thank the authors of the original paper for making their data and materials publicly available, and for their quick and helpful correspondence throughout the replication process. Any errors or issues that may remain in this replication effort are the responsibility of the Transparent Replications team.

We also owe a big thank you to our 393 research participants who made this study possible.

Finally, we are extremely grateful to the rest of the Transparent Replications team, as well as Mika Asaba and Eric Huff, for their advice and guidance throughout the project. 

Purpose of Transparent Replications by Clearer Thinking

Transparent Replications conducts replications and evaluates the transparency of randomly-selected, recently-published psychology papers in prestigious journals, with the overall aim of rewarding best practices and shifting incentives in social science toward more replicable research.

We welcome reader feedback on this report, and input on this project overall.

Appendices

Additional Information about the Methods

Error in analysis for criteria (a) and (b): χ² test of independence

The original study tested whether one version of an image was chosen more commonly than the other versions by using a χ² test of independence. 

In principle, using a χ² test of independence in this study violates one of the core assumptions of the χ² test of independence—that the observations are independent. Because participants could only choose one option for each image concept, whether a participant chose the Manipulation 1 image was necessarily dependent on whether they chose the correct image. A χ² goodness-of-fit test is the appropriate test to run when observations are not independent. 

Moreover, in order to run a χ² test of independence on this data, the authors appear to have restructured their data in a way that led to an incorrect inflation of the data, which in turn inflated the χ² values. We will use the responses for the Apple Logo image as an example to explain why the results reported in the paper were incorrect. 

In the original data, among the 100 participants who evaluated the Apple Logo, 80 participants chose the correct image, 17 chose the Manipulation 1 image, and 3 chose the Manipulation 2 image. The goal of the χ² analysis was to assess whether participants chose the Manipulation 1 image at a higher rate than the correct image. So, one way to do this analysis correctly would be to compare the proportion of participants who chose the correct image (80 out of 97) and the proportion of participants who chose the Manipulation 1 image (17 out of 97) to the proportions expected by chance (48.5 out of 97). The contingency table for this analysis should look like:

Response	Number of participants
Correct	80
Manipulation 1	17

However, because the MatLab function that was used in the paper to conduct the χ² test of independence required data input for two independent variables, the contingency table that their analysis relied on looked like this:

Response	Number of participants who provided this response	Number of participants who did not provide this response
Correct	80	20
Manipulation 1	17	83

In other words, the original study seems to have added another column that represented the total sample size minus the number of participants who selected a particular option. When structured this way, the χ² test of independence treats this data as if it were coming from two different variables: one variable that could take the values of “Correct” or “Manipulation 1”; another variable that could take the values of “Number of participants who provided this response” or “Number of participants who did not provide this response.” However, these are, in reality, the same variable: the image choice participants made. This is problematic because the test treats all of these cells as representing distinct groups of participants. However, the 80 participants in column 2, row 2 are in fact 80 of the 83 participants in column 3, row 3. In essence, much of the data is counted twice, which then inflates the χ² test statistics. 
As mentioned earlier, the correct test to run in this situation is the χ² goodness-of-fit test, which examines  observations on one variable by comparing them to a distribution and determining if they can be statistically distinguished from the expected distribution. In this case, the test determines if the responses are different from a random chance selection between the correct and manipulation 1 responses. 

Misinterpretation of analysis for criterion (c): Split-half consistency analysis

The original study said that a split-half consistency analysis was used “to determine whether people were consistent in the image choices they made” (p. 1974-1975). Here’s how the original paper described the analysis and the results:

Participants were randomly split into two halves; for each half, the proportion of correct responses and Manipulation 1 responses was calculated for each image. We then calculated the Spearman rank correlation for each response type between the participant halves, across 10,000 random shuffles of participant halves. The mean Spearman rank correlation across the iterations for the proportion of correct responses was 0.92 (p < .0001; Fig. 3b). The mean correlation across the iterations for the proportion of Manipulation 1 responses was 0.88 (p < .0001; Fig. 3b). This suggests that people are highly consistent in what images they respond correctly and incorrectly to. In other words, just as people correctly remember the same images as each other, they also have false memories of the same images as each other. 

(Prasad & Bainbridge, 2022, p. 1975)

The paper also presents the results visually using the figures below:

The intention the paper expressed for this analysis was to assess the consistency of responses across participants, but the analysis that was conducted does not seem to us to provide any reliable information about the consistency of responses across participants beyond what is already presented in the basic histogram of the entire sample of results (Figure 2 in our report; Figure 3a in the original paper). The split-half analysis seems to us to be both unnecessary and not reliability diagnostic.

In order to understand why, it may help to ask what the data would look like if respondents were not consistent with each other on which images they got correct and incorrect.

Imagine that you have two datasets of 100 people each, and in each dataset all participants got 7 out of 40 answers incorrect. This could happen in two very different ways at the extreme. In one version, each person answered 7 random questions incorrectly out of the 40 questions. In another version there were 7 questions that everyone answered wrong and 33 questions that everyone answered correctly. It seems like the paper is attempting to use this test to show that the VME dataset is more like the second version in this example where people were getting the same 7 questions wrong, rather than everyone getting a random set of questions wrong. The point is that a generalized low level of accuracy across a set of images isn’t enough. People need to be getting the same specific images wrong in the same specific way by choosing one specific wrong answer.

This is a reasonable conceptual point about what it takes for an image to be a VME image, but the split-half analysis is not necessary to provide that evidence, because the way it’s constructed means that it doesn’t add information beyond what is already contained in the histogram.

Going back to the example above illustrates this point. Here’s what the histogram would look like if everyone answered 7 questions wrong, but those questions weren’t the same as the questions that other people answered wrong:

In the above case the questions themselves do not explain anything about the pattern of the results, since each question generates exactly the same performance. You could also get this pattern of results if 18 people answered every question wrong, and 82 people answered all of them correctly. In that case as well though, the results are driven by the characteristics of the people, not characteristics of the questions.

In the other extreme where everyone answered the exact same questions wrong, the histogram would look like this:

In this case you don’t need to know anything about the participants, because the entirety of the results is explained by characteristics of the questions. 

This extreme example illustrates the point that real data on a question like this is driven by two factors – characteristics of the questions and characteristics of the participants. When the number of correct responses for some questions differs substantially from the number of correct responses for other questions we can infer that there is something about the questions themselves that is driving at least some of that difference.

This point, that people perform systematically differently on some of these image sets than others, seems to be what the paper is focusing on when it talks about the performance of participants being consistent with each other across images. And looking at the histogram from the original study we can see that there is a lot of variation from image to image in how many people answered each image correctly:

If we sort that histogram we can more easily see how this shows a pattern of responses where people were getting the same questions correct and the same questions wrong as other people:

From the results in this histogram alone we can see that people are answering the same questions right and wrong as each other. If that wasn’t the case the bars would be much more similar in height across the graph than they are. This is enough to demonstrate that this dataset meets criterion c.

The split-half consistency analysis is an attempt to demonstrate this in a way that generates a statistical result, rather than looking at it by eye, but because of how the analysis is done it doesn’t offer reliably diagnostic answers.

What is the split-half analysis doing?

What the split-half consistency analysis is doing is essentially creating a sorted histogram like the one above for each half of the dataset separately and then comparing the two halves to see how similar the ordering of the images is between them using Spearman’s Rank Correlation. This procedure is done 10,000 times, and the average of the 10,000 values for Spearman’s Rank Correlation is the reported result.

This procedure essentially takes random draws from the same sample distribution and compares them to each other to see if they match. A major problem with this approach is that, as long as the sample size is reasonably large, this procedure will almost always result in split-halves that are quite similar to each other. This is because if the halves are randomly drawn from the whole sample, at reasonably large sample sizes, the results from the halves will be similar to the results from the sample as a whole, and thus they will be similar to each other as well. Since the split-halves approximate the dataset as a whole, the split-half procedure isn’t contributing information beyond what is already present in the histogram of the dataset as a whole. This is the same principle that allows us to draw a random sample from a population and confidently infer things about the population the random sample was drawn from. 

In this case, since the two halves of 50 are each drawn and compared 10,000 times, it shouldn’t be at all surprising that on average comparing the results for each image in each half of the sample generates extremely similar results. The halves are drawn from the same larger sample of responses, and by drawing the halves 10,000 times and taking the average, the effects of any individual random draw happening to be disproportionate are minimized. 

If the sample was too small, then we wouldn’t expect the two halves of the sample to reliably look similar to each other or similar to the sample as a whole because there would not be enough data points for the noise in the data to be reliably canceled out. 

With a large enough sample size the correlation between the two halves will be extremely strong, even if there is barely any difference in the proportions of responses for each image set, because the strength of that correlation is based on the consistency of the ordering, not on any measure of the size of the differences in accuracy between the images. As the noise is reduced by increasing the sample size, the likelihood of the ordering remaining consistent between the two halves, even at very small levels of difference between the images, increases.

The strength of the correlation coming from the consistency of the ordering is due to the way that Spearman’s Rank Correlation works. Spearman’s Rank Correlation is made to deal with ordinal data, meaning data where the sizes of the differences between the values isn’t meaningful information, only the order of the values is meaningful. It accomplishes this by rank ordering two lists of data based on another variable, and then checking to see how consistent the order of the items is between the two lists. The size of the difference between the items doesn’t factor into the strength of the correlation, only the consistency of the order. In the case of this split-half analysis the rank ordering was made by lining up the images from highest proportion correct to lowest proportion correct for each half of the respondents, and then comparing those rankings between the two halves.

Split-half analysis is not diagnostic for the hypothesis it is being used to test

Because increasing the sample size drives the split-half analysis towards always having high correlations, a high correlation is not a meaningful result for showing that the pattern of results obtained is being driven by important differences between the image sets. With a large sample size the rank ordering can remain consistent even if the differences in accuracy between the images are extremely small.

In addition to the test potentially generating extremely high correlations for results that don’t include anything that meaningfully points to VME, the test also could generate much weaker correlations in the presence of a strong VME effect under some conditions. To think about how this could happen Imagine the histogram of the data looks like this:

If the data looked like this we could interpret it as meaning that there are 2 groups of images – regular images that most people know, and VME images where people consistently choose a specific wrong answer.

At modest sample sizes, noise would make the images within each group difficult to reliably rank order relative to each other when you split the data in half. That would result in a lower Spearman’s Rank Correlation for data fitting this pattern compared to the real data, even though this data doesn’t present weaker evidence of VME than the real data. The mean Spearman’s Rank Correlation for split-half analysis on this simulated dataset run 10,001 times is 0.439, which is less than half of the 0.92 correlation reported on the real data. 

The evidence that people respond in ways that are consistent with other people in the ways that are actually relevant to the hypothesis is no weaker in this simulated data than it is in the real data. The evidence that there are properties of the images that are resulting in different response patterns is just as strong here as it is in the actual data. Despite this, the split-half consistency test would (when the sample size isn’t too large) give a result that was substantially weaker than the result on the actual data.

These features of this split-half consistency analysis make it non-diagnostic for the criterion that the paper used it to attempt to examine. The results it gives do not offer information beyond what is already present in the histogram, and the results also do not reliably correspond with the level of confidence we should have about whether criterion c is being met.

It is important to note though that this split-half analysis is also not necessary to establish that the data the paper reports meets the criteria for showing a VME in certain images. The histogram of results, chi-squared goodness of fit tests, and permutation tests establish that these images meet the paper’s 5 criteria for demonstrating a Visual Mandela Effect.

Unclear labeling of the Split-Half Figures

In the process of reproducing the analysis and running simulations of this analysis, we also realized that the graphs presenting the split-half figures in the paper are likely mislabeled. The image below is a graph of the proportion of correct responses in the original data split in half with a Spearman’s Rank Correlation of 0.92 between the halves:

In this figure the images are ordered based on their ranking in the first half of the data, and then the second half of the data is compared to see how well the rankings match. This is a reasonable visual representation of what Spearman’s Rank Correlation is doing. 

The figure above looks quite different, with much more noise, than the figure presented in the paper. It seems likely the X axis on the figure in the original paper doesn’t represent images numbered consistently between the two halves (meaning Image 1 refers to the same image in both half one and half two), but rather represents the ranks from each half, meaning that the top ranked image from each half is first, then the second, than the third, which is not the same image in each half.  The figure below shows the same data plotted that way:

We did not draw the exact same set of 10,000 split-halves that was drawn in the original analysis, so this figure is not exactly the same as the figure in the original paper, but the pattern this shows is very similar to the original figure. This figure doesn’t seem to be as useful of a representation of what is being done in the Spearman’s Rank Calculation because the ranks of the images between the two halves cannot be compared in this figure.

This may seem like a minor point, but we consider it worth noting in the appendix because a reader looking at the figure in the paper will most likely come away with the wrong impression of what the figure is showing. The figure in the original paper is labeled “Images” rather than being labeled “Rankings,” which would lead a reader to believe that it shows the images following the same ordering in both halves, when that is not the case.

Additional Information about the Results

Conducting permutation tests for criteria (d) and (e) with 6 images vs 7 images

As mentioned in the body of the report and detailed in the “Error in analysis for criteria (a) and (b): χ² test of independence” section in the Appendix, the original paper conducted the χ² test incorrectly. When the correct χ² test is conducted on the original data, only 6 of the 7 images reported to show a VME remain statistically significant (Waldo from Where’s Waldo is no longer statistically significant). As such, we ran the permutation tests used to assess criteria (d) and (e) with these 6 images to ensure that the permutation test results reported in the original study held when using only images that show statistically significant evidence of a VME. 

We used the original data and followed the same procedures detailed in the “Study and Results in Detail” section. The only difference is that, when running the permutation tests, we dropped 6 images (C-3PO, Fruit of the Loom Logo, Curious George, Mr. Monopoly, Pikachu, Volkswagen Logo) instead of 7 images (C-3PO, Fruit of the Loom Logo, Curious George, Mr. Monopoly, Pikachu, Volkswagen Logo, Waldo). 

Here are the results:

Table 5. Results for criteria (d) and (e) in the original data when dropping 7 images versus 6 images

Permutation test	Reported results (1,000 permutations): Dropping 7 images: C-3PO, Fruit of the Loom Logo, Curious George, Mr. Monopoly, Pikachu, Volkswagen Logo, Waldo (Where’s Waldo)	Reproduced results (1,000 permutations): Dropping 6 images: C-3PO, Fruit of the Loom Logo, Curious George, Mr. Monopoly, Pikachu, Volkswagen Logo
Correlation between confidence and familiarity	p = 0.540	p = 0.539
Correlation between familiarity and accuracy	p = 0.044	p = 0.051
Correlation between confidence and accuracy	p = 0.001	p = 0.002

Overall, the results are extremely similar when the 7 VME images identified in the paper are dropped versus when the 6 VME images identified in our reproduced analyses are dropped. The one notable difference is that the familiarity-accuracy permutation test goes from statistically significant to non-statistically significant. However, the p-values are quite similar: p = 0.044 and p = 0.051. In other words, the familiarity-accuracy permutation test goes from having a borderline significant p-value to a borderline non-significant p-value. We don’t consider this to be a particularly meaningful difference, especially since our replication found a strong, significant result for the familiarity-accuracy permutation test (p = 0.003). 

Another way of thinking about the difference between p = 0.044 and p = 0.051 is to understand how the p-value is calculated for these permutation tests. The p-value for these tests was equal to the proportion of permutations that had a higher correlation than the correlation for the specific permutation in which the VME images were dropped. So, since 1,000 permutations were run, a p-value of 0.044 means that 44 of the 1,000 random permutations had higher correlations than the correlation when all of the VME images were dropped. A p-value of 0.051 means that 51 of the 1,000 random permutations had higher correlations. Thus, the difference between p = 0.044 and p = 0.051 is a difference of 7 more random permutations having a higher correlation than the correlation when all of the VME images are dropped. 

Understanding how the p-value is calculated also explains why running more permutations gives the test more precision. Running more permutations affords the test a larger sample of all the possible permutations to compare against the specific permutation of interest—which, in this case, is when all of the VME images are dropped. This is why we pre-registered and ran 10,000 permutations on our replication data, rather than the 1,000 that were run in the original study. 

Correlations between accuracy, confidence, and familiarity

As discussed earlier in this report, two of the criteria the original paper used to evaluated whether images showed evidence of a VME were:

(d) the image shows low accuracy even when it is rated as being familiar
(e) the responses on the image are given with high confidence even though they are incorrect

(Prasad & Bainbridge, 2022, p. 1974)

To test criterion (d), the original paper used a permutation test to assess whether the correlation between accuracy and familiarity was higher when the 7 images that met criteria (a) and (b) were excluded compared to when other random sets of 7 images were excluded. Similarly, to test criterion (e), the original paper used a permutation test to assess whether the correlation between accuracy and confidence was higher when the 7 images that met criteria (a) and (b) were excluded compared to when other random sets of 7 images were excluded.

In order to calculate the correlations between accuracy and familiarity and between accuracy and confidence, the original paper first calculated the average familiarity rating, confidence rating, and accuracy for each of the 40 images. The correlation of interest was then calculated using these average ratings for the 40 images. In other words, each correlation tested 40 data points. We will refer to this as the image-level approach.

Another way of running this correlation would be to use each rating from each participant as a single data point in the correlation. For every image, participants made a correct or incorrect choice, and they rated their confidence in the choice and their familiarity with the image. Thus, the correlation could have been run using each of these sets of ratings. 100 participants completed the original study, rating 40 images each, which means each correlation would have tested close to 4,000 data points (it wouldn’t have been exactly 4,000 data points because a few participants did not rate all 40 images.)  

While the image-level approach is not necessarily incorrect, we argue that it sacrifices granularity in a way that could, in principle, be misleading. Here’s an extreme example to demonstrate this:

Imagine you run the VME study twice (Study A and Study B), and in each study, you only have 2 participants (participants 1-4). For the Mr. Monopoly image in Study A, participant 1 chooses the incorrect image (accuracy = 0) and gives the lowest possible confidence rating (confidence = 1). Meanwhile, participant 2 in Study A chooses the correct image (accuracy = 1) for Mr. Monopoly and gives the highest possible confidence rating (confidence = 5). If you take the image-level average for each of these variables, you will have an accuracy rating of 0.5 and a confidence rating of 3 for Mr. Monopoly in Study A. Now, in Study B, participant 3 chooses the incorrect image (accuracy = 0) for Mr. Monopoly, but gives the highest possible confidence rating (confidence = 5), and participant 4 chooses the correct image (accuracy = 1) for Mr. Monopoly, but gives the lowest possible confidence rating (confidence = 1). If you take the image-level average for each of these variables, you will have the exact same scores for Mr. Monopoly as you did in Study A: an accuracy rating of 0.5 and a confidence rating of 3. However, these two studies have the exact opposite pattern of results (see Table 6). Averaging at the image level before correlating these ratings across the 40 images means that such differences are impossible to detect in the correlation. However, if each individual set of ratings is included in the correlation, the analysis can account for these differences. Although it’s unlikely, it is possible that the image-level approach could give the same correlation to two different datasets that would have correlations in opposite directions if the individual-level approach was used.  

Table 6. Hypothetical scores to demonstrate that averaging at the image-level before running a correlation could mask important individual-level differences 

Hypothetical Study A			Hypothetical Study B
Participant	Accuracy	Confidence	Participant	Accuracy	Confidence
1	0	1	3	0	5
2	1	5	4	1	1
Average score	0.5	3	Average score	0.5	3

Given this limitation of the image-level approach, we decided to re-run the correlations and permutation tests using the individual-level approach. We did so for both the original data and our replication data. To account for the repeated-measures nature of the individual-level data (each participant provided multiple responses), we ran repeated-measures correlations (Bakdash & Marusich, 2017) rather than Pearson correlations. You can see the results from these analyses in Table 7. 

One important thing to note is that the data for the original paper was structured such that it was not possible to know, with 100% certainty, which ratings were from the same participants. The original data was formatted as 4 separate .csv files—one file for each measure (image choice, confidence rating, familiarity rating, times-seen rating)—with no participant-ID variable. In order to conduct this analysis, we had to assume that participants’ data were included in the same row in each of these files. For example, we assumed the data in row 1 in each of the four files came from the same participant. This was a big limitation of the format in which the data was shared. However, the differences in results between the image-level approach and the individual-level approach are quite similar among both the original data and the replication data. This suggests that we were correct to assume that each row in the original data files came from the same participant. 

Table 7. Comparison of correlations for the image-level approach versus the individual-level approach

Test	Original data	Original data	Replication data	Replication data
	Image-level correlation (Pearson’s r)	Individual-level correlation (repeated-measures correlation)	Image-level correlation (Pearson’s r)	Individual-level correlation (repeated-measures correlation)
Correlation: confidence and familiarity	r = 0.90	r = 0.68	r = 0.90	r = 0.74
Correlation: familiarity and accuracy	r = 0.42	r = 0.18	r = 0.35	r = 0.23
Correlation: confidence and accuracy	r = 0.59	r = 0.25	r = 0.58	r = 0.33

Fortunately, the differences between the image-level results and the individual-level results were either minimal or directionally consistent. For example, the difference between the confidence-accuracy correlation in the original data when calculated with these two methods is fairly large: r = 0.59 vs r = 0.25. However, these correlations are directionally consistent (both positive), and the results for the confidence-accuracy permutation tests in the original data are very similar for the two methods: p = 0.001 and p = 0.007. 

Table 8. Comparison of permutation test results for the image-level approach versus the individual-level approach

Test	Original data:	Original data:	Replication data:	Replication data:
	Image-level (7 images removed; 1,000 permutations)	Individual-level(7 images removed; 1,000 permutations)	Image-level(8 images removed; 10,000 permutations)	Individual-level(8 images removed; 10,000 permutations)
Permutation test: confidence and familiarity	p = 0.540	p = 0.100	p = 0.320	p = 0.067
Permutation test: familiarity and accuracy	p = 0.044	p = 0.016	p = 0.003	p = 0.001
Permutation test: confidence and accuracy	p = 0.001	p = 0.007	p = 0.000	p = 0.000

Wilcoxon Rank Sum test

The original study reports:

There was also no significant difference between the number of times that participants had seen VME-apparent images and the number of times they had seen the images that were correctly identified (Wilcoxon rank sum; z = 0.64, p = .523), supporting the idea that there is no difference in prior exposure between VME-apparent images that induce false memory and images that do not.

(Prasad & Bainbridge, 2022, p. 1977)

We attempted to reproduce this analysis using the original data, but were unable to find the same results. Below, we describe the seven different ways we tried running this test. 

There are two important things to contextualize these different ways of running this analysis. First, in the original data file, the responses on the Times Seen measure have values of 0, 1, 11, 51, 101, or 1000 (the response options participants saw for this measure were 0; 1-10; 11-50; 51-100; 101-1000; 1000+). Second, technically a Wilcoxon Rank Sum test assumes independent samples while a Wilcoxon Signed Rank test assumes paired samples (e.g., repeated measures). As shown in the quote above, the paper reports that a Wilcoxon Rank Sum test was run. 

1. Individual level (Wilcoxon Rank Sum)

We ran a Wilcoxon Rank Sum test on the individual level data (i.e., the data was not aggregated in any way) comparing the Times Seen ratings on VME images versus non-VME images. The results were: W = 1266471, p = 2.421e-07. 

2. Image level – recoded (Wilcoxon Rank Sum)

Another way to analyze this data, consistent with the other analyses the paper reported, is to first calculate the average rating for each image, and then run the test with these image-level values. One potential hiccup in this case is that the values for the Times Seen measure in the original data files were 0, 1, 11, 51, 101, or 1000. It seems problematic to simply average these numbers since the actual options participants chose from were ranges (e.g., 101-1000). If a participant selected 101-1000, they could have seen the image 150 times or 950 times. Treating this response as always having a value of 101 seems incorrect. So, we reasoned that perhaps the authors had first recoded these values to simply be 0, 1, 2, 3, 4, and 5 rather than 0, 1, 11, 51, 101, and 1000. 

Thus, we first recoded the variable to have values of 0, 1, 2, 3, 4, and 5 rather than 0, 1, 11, 51, 101, and 1000. We then calculated the average rating for each image. We then ran a Wilcoxon Rank Sum test with these image-level values comparing the Times Seen ratings on VME images versus non-VME images. The results were: W = 163.5, p = 0.091.

3. Image level – not recoded (Wilcoxon Rank Sum)

It also seemed plausible that the authors had not recoded these values before calculating the average rating for each image. So, we also tried this approach by calculating the average rating for each image (without recoding the values), and then running a Wilcoxon Rank Sum test comparing the Times Seen ratings on VME images versus non-VME images. The results were: W = 164, p = 0.088.

4. Within-individual aggregation – recoded (Wilcoxon Rank Sum)

Another way of aggregating the data is to calculate an average value of the Times Seen measure for the VME images and the non-VME images within each participant’s data. In other words, each participant would have an average Times Seen rating for the 7 VME images and an average Times Seen rating for the 33 non-VME images. As with aggregating at the image-level, this raises the question of whether the data should be recoded first. 

In this analysis, we first recoded the variable to have values of 0, 1, 2, 3, 4, and 5 rather than 0, 1, 11, 51, 101, and 1000. We then calculated the average Times Seen rating for VME-images for each participant and the average Times Seen rating for non-VME-images for each participant. We then ran a Wilcoxon Rank Sum test with these within-individual aggregated values comparing the Times Seen ratings on VME images versus non-VME images. The results were: W = 5854.5, p = 0.037. 

5. Within-individual aggregation – recoded (Signed Rank)

Because of the structure of the Within-individual aggregated data described in test #4, it was also possible to run a Wilcoxon Signed Rank test rather than a Wilcoxon Rank Sum test. We reasoned that it was possible that the original paper used a Wilcoxon Signed Rank test, but it was mislabeled as a Wilcoxon Rank Sum test. 

In this analysis, we followed the same steps as in test #4, but we ran a Wilcoxon Signed Rank test rather than a Wilcoxon Rank Sum test—in other words, we treated the data as paired samples, rather than independent samples. (In the case of this study, treating the data as paired samples is actually correct since participants rated both VME images and non-VME images.) The results were: V = 4002.5, p = 3.805e-07. 

6. Within-individual aggregation – not recoded (Wilcoxon Rank Sum)

We also attempted test #4 without recoding the values. The results were: W = 6078, p = 0.008

7. Within-individual aggregation – not recoded (Wilcoxon Rank Sum)

We also attempted test #5 without recoding the values. The results were: V = 4030, p = 2.304e-07

As you can see by comparing the p-values, we were not able to reproduce the specific results reported in the paper using the original data. The original paper found a null result on this test. Two versions of our analysis also found null results (although with much smaller p-values than what was reported in the paper). These two versions used image-level averages of the Times Seen rating. If image-level averages were used for conducting this test, that would have the same flaw as the permutation test analyses: averaging at the image level before conducting these analyses sacrifices granularity in a way that could, in principle, be misleading (see the “Correlations between accuracy, confidence, and familiarity” in the Appendix for more information). 

We tried running the test in several ways in an attempt to reproduce the original result. Given that we were unable to reproduce that result, it seems likely that none of these seven ways we attempted to run the test matched how the test was run in the original study. The authors reported that they used the ranksum function in MatLab to run the test, but we were unable to determine how the data was structured as input to this function. Without access to the original analysis code or a more detailed description in the paper, we cannot be sure why we were unable to reproduce the original results.  

References

Bakdash, J. Z. & Marusich, L. R. (2017). Repeated measures correlation. Frontiers in Psychology, 8, 456. https://doi.org/10.3389/fpsyg.2017.00456

Faul, F., Erdfelder, E., Buchner, A., & Lang, A.-G. (2009). Statistical power analyses using G*Power 3.1: Tests for correlation and regression analyses. Behavior Research Methods, 41, 1149-1160. Download PDF

Prasad, D., & Bainbridge, W. A. (2022). The Visual Mandela Effect as Evidence for Shared and Specific False Memories Across People. Psychological Science, 33(12), 1971–1988. https://doi.org/10.1177/09567976221108944

Executive Summary

Transparency	Replicability	Clarity
	1 of 1 findings replicated

We ran a replication of study 4a from this paper, which found that people underestimate how much their acquaintances would appreciate it if they reached out to them. This finding was replicated in our study. 

The study asked participants to think of an acquaintance with whom they have pleasant interactions, and then randomized the participants into two conditions – Initiator and Responder. In the Initiator condition, participants answered questions about how much they believe that their acquaintance would appreciate being reached out to by the participant. In the responder condition, participants answered questions about how much they would appreciate it if their acquaintance reached out to them. Participants in the Responder condition reported that they would feel a higher level of appreciation if they were reached out to than participants in the Initiator condition reported they expected their acquaintance would feel if the participant reached out to them. Appreciation here was measured by an average of four questions which asked how much the reach-out would be appreciated by the recipient, and how thankful, grateful, and pleased it would make the recipient feel.

The original study received a high transparency rating because it followed a pre-registered plan, and the methods, data, and analysis code were publicly available. The original study reported one main finding, and that finding replicated in our study. The study’s clarity could have been improved if the paper had not stated that the reaching out in the study was through a “brief message,” because in the actual study, the nature of the outreach was not specified. Apart from that relatively minor issue, the study’s methods, results, and discussion were presented clearly and the claims made were well-supported by the evidence provided.

Full Report

Study Diagram

Replication Conducted

We ran a replication of Study 4a from: Liu, P.J., Rim, S., Min, L., Min K.E. (2023). The Surprise of Reaching Out: Appreciated More Than We Think. Journal of Personality and Social Psychology, 124(4), 754–771. https://doi.org/10.1037/pspi0000402 

How to cite this replication report: Transparent Replications by Clearer Thinking. (2023). Report #7: Replication of a study from “The Surprise of Reaching Out: Appreciated More Than We Think” (JPSP | Liu et al. 2023) https://replications.clearerthinking.org/replication-2023jpsp124-4
(Preprint DOI: https://doi.org/10.31234/osf.io/gxvdr)

Key Links

• Our Research Box for this replication report includes the pre-registration, study materials, de-identified data, and analysis files.
• Download a PDF of the original paper.
• Review the supplemental materials and the Research Box for the original paper.

Overall Ratings

To what degree was the original study transparent, replicable, and clear?

Transparency:  how transparent was the original study?	All of the materials were publicly available. The study was pre-registered, and the pre-registration was followed.
Replicability: to what extent were we able to replicate the findings of the original study?	This study had one main finding, and that result replicated.
Clarity: how unlikely is it that the study will be misinterpreted?	This study was mostly clear and easy to interpret. The one area where clarity could have been improved is in the description of the type of reaching out in the study as a “brief message” in the paper, when the type of reaching out was not specified in the study itself.

Detailed Transparency Ratings

Overall Transparency Rating:
1. Methods Transparency:	The experimental materials are publicly available.
2. Analysis Transparency:	The analysis code is publicly available.
3. Data availability:	The data are publicly available.
4. Preregistration:	The study was pre-registered, and the pre-registration was followed.

Summary of Study and Results

In both the original study and our replication study, participants were asked to provide the initials of a person who they typically have pleasant encounters with who they consider to be a “weak-tie” acquaintance. Participants were then randomly assigned to either the “Initiator” condition or the “Responder” condition.

In the Initiator condition, participants were told to imagine that they happened to be thinking of the person whose initials they provided, and that they hadn’t spent time with that person in awhile. They were told to imagine that they were considering reaching out to this person. Then they were asked four questions:

If you reached out to {Initials}, to what extent would {Initials}…

• appreciate it?
• feel grateful?
• feel thankful?
• feel pleased?

In the Responder condition, participants were told to imagine that the person whose initials they provided happened to be thinking of them, and that they hadn’t spent time with that person in awhile. They were told to imagine that this person reached out to them. Then they were asked four questions:

If {Initials} reached out to you, to what extent would you…

• appreciate it?
• feel grateful?
• feel thankful?
• feel pleased?

In both conditions, responses to these four questions were on a Likert scale from 1-7, with 1 labeled “not at all” and 7 labeled “to a great extent.” For both conditions, the responses to these four questions were averaged to form the dependent variable, the “appreciation index.”

The key hypothesis being tested in this experiment and the other experiments in this paper is that when people consider reaching out to someone else, they underestimate the degree to which the person receiving the outreach would appreciate it. 

In this study, that hypothesis was tested with an independent-samples t-test comparing the appreciation index between the two experimental conditions.

The original study found a statistically significant difference between the appreciation index in the two groups, with the Responder group’s appreciation index being higher. We found the same result in our replication study.  

Hypothesis	Original results	Our results	Replicated?
Initiators underestimate the degree to which responders appreciate being reached out to.	+	+	✅

Study and Results in Detail

The table below shows the t-test results for the original study and our replication study.

Original results (n = 201)	Our results (n = 742)	Replicated?
Minitiator = 4.36, SD = 1.31 Mresponder = 4.81, SD = 1.53 Mdifference = −.45 95% CI [−.84, −.05] t(199) = −2.23 p = .027 Cohen’s  d = .32	Minitiator = 4.46, SD = 1.17 Mresponder = 4.77, SD = 1.28 Mdifference = −.30 95% CI [−.48, −.13] t(740) = −3.37 p < .001 Cohen’s  d = .25	✅

Additional test conducted due to assumption checks

When we reproduced the results from the original study data, we conducted a Shapiro-Wilk Test of Normality, and noticed that the pattern of responses in the dependent variable for the Responder group deviated from a normal distribution. The t-test assumes that the means of the distributions being compared follow normal distributions, so we also ran a Mann-Whitney U test on the original data and found that test also produced statistically significant results consistent with the t-test results reported in the paper. (Note: some would argue that we did not need to conduct this additional test because the observations themselves do not need to be normally distributed, and for large sample sizes, the normality of the means can be assumed due to the central limit theorem.)  

After noticing the non-normality in the original data, we included in our pre-registration a plan to also conduct a Mann-Whitney U test on the replication data if the assumption of normality was violated. We used the Shapiro-Wilk Test of Normality, and found that the data in both groups deviated from normality in our replication data. As was the case with the original data, we found that the Mann-Whitney U results on the replication data were also statistically significant and consistent with the t-test results.

Mann-Whitney U – original data	Mann-Whitney U – replication data	Replicated?
Test statistic = 4025.500 p = .013 Effect size = .203 (rank biserial correlation)	Test statistic = 58408.000 p < .001 Effect size = .151 (rank biserial correlation)	✅

We also ran Levene’s test for equality of variances on both the original data and the replication data, since equality of variances is an additional assumption of Student’s t. We found that both the original data and the replication data met the assumption of equality of variances. The variance around the mean was not statistically significantly different between the two experimental conditions in either dataset.

Effect sizes and statistical power

The original study reported an effect size of d = 0.32, which the authors noted in the paper was smaller than the effect size required for the study to have 80% power. This statistical power concern was presented clearly in the paper, and the authors also mentioned it when we contacted them about conducting a replication of this study. We dramatically increased the sample size for our replication study in order to provide more statistical power.

We set our sample size so that we would have a 90% chance to detect an effect size as small as 75% of the effect size detected in the original study. Using G*Power, we determined that to have 90% power to detect d = 0.24 (75% of 0.32), we needed a sample size of 732 (366 for each of the two conditions). Due to the data collection process in the Positly platform, we ended up with 10 more responses than the minimum number we needed to collect. We had 742 participants (370 in the Initiator condition, and 372 in the Responder condition).

The effect size in the replication study was d = 0.25. Our study design was adequately powered for the effect size that we obtained.

Interpreting the Results

This finding replicating on a larger sample size with higher statistical power increases our confidence that this result is not due to a statistical artifact. The key hypothesis that recipients of reaching out appreciate it more than initiators predict that they will is supported by our replication findings.

There is a possible alternative explanation for the results of this study – it is possible that participants think of acquaintances that they’d really like to hear from, and they aren’t sure that this particular acquaintance would be as interested in hearing from them.  Although this study design does not rule out that explanation, this is only one of the 13 studies reported on in this paper. Studies 1, 2, and 3 have different designs and test the same key hypothesis. Study 1 in the paper uses a recall design in which people are assigned to either remember a time they reached out to someone or a time that someone reached out to them, and then answer questions about how much they appreciated the outreach. In Study 1 there were also control questions about the type of outreach, how long ago it was, and the current level of closeness of the relationship. The Initiator group and the Responder group in that study were not significantly different from each other on those control questions, suggesting that the kinds of reaching out situations that people were recalling were similar between the Initiator and Responder groups in Study 1. Since the recall paradigm presents its own potential for alternative explanations, the authors also did two field studies in which they had college student participants write a short message (Study 2) or a write short message and include a small gift (Study 3) reaching out to a friend on campus who they hadn’t spoken to in awhile. The student participants predicted how much the recipients would appreciate them reaching out. The experimenters then contacted those recipients, passed along the messages and gifts, and asked the recipients questions about how much they appreciated being reached out to by their friend. Studies 2 and 3 used paired samples t-tests to compare across initiator-recipient dyads, and found that the recipients appreciated the outreach more than the initiators of the outreach predicted they would. Studies 4a (replicated here) and 4b use a scenario paradigm to create greater experimental control than the field study allowed. The authors found consistent results in the recall, dyadic field experiments, and scenario studies, which allowed them to provide clearer evidence supporting their hypothesis over possible alternative explanations.

Later studies in this paper test the authors’ proposed mechanism – that people are surprised when someone reaches out to them. The authors propose that the pleasant surprise experienced by the recipients increases their appreciation for being reached out to, but initiators don’t take the surprise factor into account when attempting to predict how much their reaching out will be appreciated. Studies 5a-b, 6, 7, and supplemental studies S2,S3, and S4 all test aspects of this proposed mechanism. Testing these claims was beyond the scope of this replication effort, but understanding the mechanism the authors propose is useful for interpreting the results of the replication study we conducted.

The one issue with the way that study 4a is described in the paper is that the authors describe the study as involving reaching out with a “brief message,” but the study itself does not specify the nature of the outreach or its content. When describing studies 4a and 4b the authors say, “We then controlled the content of initiators’ reach-out by having initiators and responders imagine the same reach-out made by initiators.” While this is true for study 4b, in which the reach-out is described as one of a few specific small gifts, it is not the case for study 4a, which simply asks participants to imagine either that they are considering reaching out, or that their acquaintance has reached out to them. The description of the study in the paper is likely to lead readers to a mistaken understanding of what participants were told in the study itself. This reduced the clarity of this study; however, the issue is mitigated somewhat by the fact that there is another study in the paper (study S1) with similar results that does involve a specified brief message as the reach-out.

In interpreting the results of this study it is also important to recognize that although the finding is statistically significant, the effect size is small. When drawing substantive conclusions about these results it is important to keep the effect size in mind.

Conclusion

This pre-registered study provided a simple and clear test of its key hypothesis, and the finding replicated on a larger sample size in our replication. The study materials, data, and code were all provided publicly, and this transparency made the replication easy to conduct. The one area in which the clarity of the study could have been improved is that the paper should not have described the type of reaching out being studied as a “brief message,” because the type of reaching out was not specified in the study itself. Apart from this minor issue, the methods, results and discussion of the study were clear and the claims made were supported by the evidence provided.

Acknowledgements

We are grateful to the authors for their responsiveness in answering questions about this replication, and for making their methods, analysis, and materials publicly available. Their commitment to open science practices made this replication much easier to conduct than it would have been otherwise. 

I want to thank Clare Harris and Spencer Greenberg at Transparent Replications for their feedback on this replication and report. Also, thank you to the Ethics Evaluator who reviewed our study plan.

Lastly, thank you to the 742 participants in this study, without whose time and attention this work wouldn’t be possible.

Purpose of Transparent Replications by Clearer Thinking

Transparent Replications conducts replications and evaluates the transparency of randomly-selected, recently-published psychology papers in prestigious journals, with the overall aim of rewarding best practices and shifting incentives in social science toward more replicable research.

We welcome reader feedback on this report, and input on this project overall.

References

Faul, F., Erdfelder, E., Buchner, A., & Lang, A.-G. (2009). Statistical power analyses using G*Power 3.1: Tests for correlation and regression analyses. Behavior Research Methods, 41, 1149-1160. Download PDF

Liu, P.J., Rim, S., Min, L., Min K.E. (2023). The Surprise of Reaching Out: Appreciated More Than We Think. Journal of Personality and Social Psychology, 124(4), 754–771. https://doi.org/10.1037/pspi0000402

​​Executive Summary

Transparency	Replicability	Clarity
	9 of 10 findings replicated

We ran a replication of study 4 from this paper, which found that people’s perceptions of an artwork as sacred are shaped by collective transcendence beliefs (“beliefs that an object links the collective to something larger and more important than the self, spanning space and time”). 

In the study, participants viewed an image of a painting and read a paragraph about it. All participants saw the same painting, but depending on the experimental condition, the paragraph was designed to make it seem spiritually significant, historically significant, both, or neither. Participants then answered questions about how they perceived the artwork. 

Most of the original study’s methods and data were shared transparently, but the exclusion procedures and related data were only partially available. Most (90%) of the original study’s findings replicated. In both the original study and our replication, “collective meaning” (i.e., the perception that the artwork has a “deeper meaning to a vast number of people”) was found to mediate the relationships between all the experimental conditions and the perceived sacredness of the artwork. The original study’s discussion was partly contradicted by its mediation results table, and the control condition, which was meant to control for uniqueness, did not do so; the original paper would have been clearer if it had addressed these points.

Full Report

Study Diagram

Replication Conducted

We ran a replication of Study 4 from: 

Chen, S., Ruttan, R. L., & Feinberg, M. (2022). Collective transcendence beliefs shape the sacredness of objects: The case of art. Journal of Personality and Social Psychology. 124(3), 521–543. https://doi.org/10.1037/pspa0000319 

How to cite this replication report: 

Transparent Replications by Clearer Thinking. (2023). Report #6: Replication of a study from “Collective transcendence beliefs shape the sacredness of objects: The case of art” (JPSP | Chen, Ruttan, & Feinberg, 2023). https://replications.clearerthinking.org/replication-2022jpsp124-3
(Preprint DOI: https://doi.org/10.31234/osf.io/cz985

Key Links

• Our Research Box for this replication report includes the pre-registration, study materials, de-identified data, and analysis files.
• The Metaculus prediction page about this study attracted a total of 23 predictions from 11 participants. The median prediction was that 5 of the 10 findings would replicate. However, participants also commented that they struggled with the forecasting instructions.
• Request a PDF of the original paper from the authors.
• The data and pre-registration for the original study can be found on the Open Science Framework (OSF) site.

Overall Ratings

To what degree was the original study transparent, replicable, and clear?

Transparency: how transparent was the original study?	Most of the study materials and data were shared transparently, except for the exclusion-related procedures and data. There were some minor deviations from the pre-registered study plan.
Replicability: to what extent were we able to replicate the findings of the original study?	9 of the 10 original findings replicated (90%).
Clarity: how unlikely is it that the study will be misinterpreted?	The discussion of “uniqueness” as an alternative mediator is not presented consistently between the text and the results tables, and the failure of the control condition to successfully manipulate uniqueness is not acknowledged clearly in the discussion.

Detailed Transparency Ratings

Overall Transparency Rating
1. Methods transparency:	The materials were publicly available and almost complete; not all the remaining materials were provided on request because the Research Assistants had been trained in person by the lead author, but this did not significantly impact our ability to replicate the study. We were able to locate or be provided with all materials required to run and process the data for this study, except for the exclusion procedures, which were only partially replicable. We requested the specific instructions given to the hypothesis-blinded coders for exclusion criterion #3 (see appendices), but those materials were not available.
2. Analysis transparency	Some of the analyses were commonly-completed analyses that were described fully enough in the paper to be able to replicate without sharing code. The conditional process analysis was described in the paper and was almost complete, and the remaining details were given on request. However, the original random seed that was chosen had not been saved.
3. Data availability:	The data were publicly available and partially complete, but the remaining data (the data for the free-text questions that were used to include/exclude participants in the original study) were not accessible.
4. Pre-registration:	The study was pre-registered and was carried out with minor deviations, but those deviations were not acknowledged in the paper. In the pre-registration, the authors had said they would conduct more mediation analyses than they reported on in the paper (see the appendices). There were also some minor wording changes (e.g., typo corrections) that the authors made between the pre-registration and running the study. While these would be unlikely to impact the results, ideally they would have been noted.

Summary of Study and Results

Summary of the study

In the original study and in our replication, U.S. adults on MTurk were invited to participate in a “study about art.” After completing an informed consent form, all participants were shown an image of an artwork called “The Lotus,” accompanied by some text. The text content was determined by the condition to which they were randomized. In the original study, participants were randomized to one of four conditions (minimum number of participants per condition after exclusions: 193). 

Depending on the condition, participants read that the artwork was…

1. ….both historically and spiritually significant (this condition combined elements from conditions 2 and 3 [described in the following lines]);
2. …over 900 years old (according to radiocarbon dating) and “serves as a record of human history;” 
3. …aiming to depict key spiritual aspects of Buddhism, a religion that helps people to connect to a “higher power of the universe;” or:
4. …unique because it was painted in 10 minutes by a talented artist and because of aspects of its artistic style.

In our replication, we had at least 294 participants per condition (after exclusions). Participants were randomized to one of five conditions. Four of the conditions were replications of the four conditions described above, and the fifth condition was included for the purposes of additional analyses. The fifth condition does not affect the replication of the study (as the participants randomized to the other four conditions are not affected by the additional fifth condition). In the fifth condition, participants read that the artwork was unique because it was created by a child prodigy using one-of-a-kind paints created specifically for the artwork that would not be created again. 

All participants answered a series of questions about the artwork. They were asked to “indicate how well you think the following statements describe your feelings and beliefs about this piece of art:” (on a scale from “Strongly disagree (1)” to “Strongly agree (7)”). The questions captured participants’ views on the artwork’s sacredness, collective meaning, uniqueness, and usefulness, as well as participants’ positive or negative emotional response to the artwork. Sacredness in this context was defined as the perception that the artwork was “absolute and uncompromisable,” and unable to be “thought of in cost–benefit terms.” A complete list of the questions is in the “Study and Results in Detail” section.

Summary of the results

The original study tested 10 hypotheses (which we refer to here as Hypothesis 1 to Hypothesis 10, or H1 to H10 for short). They are listed in the table below, along with the original results and our replication results. (Please see the Study and Results in Detail section for an explanation of how the hypotheses were tested, as well as an explanation of the specific results.)

Hypotheses	Original results	Our results	Replicated?
H1: Art with higher historical significance and collective spirituality will be rated as more collectively meaningful, compared to a control condition.	+  (Positive finding)	+  (Positive finding)	✅
H2: Art with higher historical significance will be rated as more collectively meaningful, compared to a control condition.	+	+	✅
H3: Art with higher collective spirituality will be rated as more collectively meaningful, compared to a control condition.	+	+	✅
H4: Art with higher historical significance and collective spirituality will be rated as more sacred, compared to a control condition.	+	+	✅
H5: Art with higher historical significance will be rated as more sacred, compared to a control condition.	+	+	✅
H6: Art with higher collective spirituality will be rated as more sacred, compared to a control condition.	+	+	✅
H7: H4 will be mediated by H1.	+	+	✅
H8: H5 will be mediated by H2.	+	+	✅
H9: H6 will be mediated by H3.	+	+	✅
H10: H4, H5, and H6 will not be mediated by other alternative mediators, including positivity, negativity, personal meaning, and utility of the painting.	– (Partially contradicted)	— (Mostly contradicted)	❌

Study and Results in Detail

The questions included in the study are listed below. We used the same questions, including the same (in some cases unusual) punctuation and formatting, as the original study.

• Manipulation check questions:
  • I believe, for many people this work of art evokes something profoundly spiritual.
  • I believe, this work of art is a reflection of the past – a record of history.
  • I believe, this piece of art is unique.
• Alternative mediator questions:
  • Usefulness questions:
    • This piece of art is useful for everyday use.
    • You can use this piece of art in everyday life in a lot of different ways.
    • This piece of art is functional for everyday use.
    • I believe, this piece of art is unique.
  • This piece of art makes me feel positive.
  • This piece of art makes me feel negative.
  • I personally find deep meaning in this piece of art that is related to my own life.
• Collective meaning questions:
  • It represents something beyond the work itself – this work of art has deeper meaning to a vast number of people.
  • A lot of people find deep meaning in this work of art– something more than what is shown in the painting.
  • For many people this work of art represents something much more meaningful than the art itself.
• Sacredness questions:
  • This piece of art is sacred.
  • I revere this piece of art.
  • This piece of art should not be compromised, no matter the benefits (money or otherwise).
  • Although incredibly valuable, it would be inappropriate to put a price on this piece of art.

There were two order sequences:

• Participants answered questions about: (1) manipulation checks, (2) collective meaning, (3) alternative mediators, (4) sacredness
• Participants answered questions about: (1) manipulation checks, (2) sacredness, (3) alternative mediators, (4) collective meaning

Both our study and the original randomized each participant to one of the two order sequences above. In contrast to the original study, we also randomized the order of presentation of the questions within each set of questions. 

In both the original study and in our replication, participants were excluded if any of the following conditions applied: 

1. They had missing data on any of the variables of interest
2. They failed to report “the Lotus” (with or without a capital, and with or without “the”) when asked to provide the name of the artwork that they had been presented with 
3. They either failed to provide any information or provided random information that was irrelevant to details about the painting (as judged by two coders blinded to the study hypotheses, with the first author making the final decision in cases where the two coders disagreed). Please see the appendices for additional information about this.
4. They report having seen or read about the artwork prior to completing the study (in response to the question, “Prior to this study, did you know anything about the artwork that you read about in this study? If so, what was your prior knowledge?”)

Testing Hypotheses 1-6

To test Hypotheses 1-6, both the original study and our replication used one-way analyses of variance (ANOVAs) with experimental condition as the between-subjects factor and with each measured variable (in turn) as the dependent variable. This was followed up with independent samples t-tests comparing the collective meaning and sacredness of each treatment condition to the control condition. We performed our analyses for Hypotheses 1-6 in Jasp (Jasp Team, 2020; Jasp Team, 2023).

Tables showing all of the t-test results are available in the appendix. The t-test results for the collective meaning-related hypotheses (1-3), and the sacredness-related hypotheses (4-6) are shown below.

Results for Hypotheses 1-6

Collective Meaning Hypotheses	Original results	Our results
H1: Art with higher historical significance and collective spirituality will be rated as more collectively meaningful, compared to a control condition.	Mcontrol  (SD) = 4.50 (1.31) Mcombined (SD) = 5.66 (.98) t = 10.65  p < 0.001 Cohen’s d = 1.06	Mcontrol  (SD) = 4.19 (1.45) Mcombined (SD) = 5.75 (1.09) t = 15.1 p < 0.001 Cohen’s d = 1.22	✅
H2: Art with higher historical significance will be rated as more collectively meaningful, compared to a control condition.	Mcontrol  (SD) = 4.50 (1.31) Mhistorical (SD) = 5.22 (1.08) t = 6.38 p < 0.001 Cohen’s d = 0.64	Mcontrol  (SD) = 4.19 (1.45) Mhistorical (SD) = 5.37 (1.22) t = 11.03 p < 0.001 Cohen’s d = 0.89	✅
H3: Art with higher collective spirituality will be rated as more collectively meaningful, compared to a control condition.	Mcontrol  (SD) = 4.50 (1.31) Mspiritual (SD) = 5.78 (1.06) t = 11.6 p < 0.001 Cohen’s d = 1.16	Mcontrol  (SD) = 4.19 (1.45) Mspiritual (SD) = 5.73 (1.16) t = 14.46 p < 0.001 Cohen’s d = 1.17	✅

Sacredness Hypotheses	Original results	Our results
H4: Art with higher historical significance and collective spirituality will be rated as more sacred, compared to a control condition.	Mcontrol  (SD) = 3.49 (1.13) Mcombined (SD) = 4.71 (1.03) t = 11.33 p < 0.001 Cohen’s d = 1.13	Mcontrol  (SD) = 3.08 (1.16) Mcombined (SD) = 4.72 (1.30) t = 16.41 p < 0.001 Cohen’s d = 1.33	✅
H5: Art with higher historical significance will be rated as more sacred, compared to a control condition.	Mcontrol  (SD) = 3.49 (1.13) Mhistorical (SD) = 4.55 (1.08) t = 9.59 p < 0.001 Cohen’s d = 0.96	Mcontrol  (SD) = 3.08 (1.16) Mhistorical (SD) = 4.69 (1.28) t = 16.37 p < 0.001 Cohen’s d = 1.31	✅
H6: Art with higher collective spirituality will be rated as more sacred, compared to a control condition.	Mcontrol  (SD) = 3.49 (1.13) Mspiritual (SD) = 4.13 (1.18) t = 5.85 p < 0.001 Cohen’s d = 0.59	Mcontrol  (SD) = 3.08 (1.16) Mspiritual (SD) = 3.90 (1.30) t = 8.15 p < 0.001 Cohen’s d = 0.66	✅

Conditional Process Analysis

Hypotheses 7-10 were assessed using a particular kind of mediation analysis known as multicategorical conditional process analysis, following Andrew Hayes’ PROCESS model. It is described in his book Introduction to Mediation, Moderation, and Conditional Process Analysis: A Regression-based Approach. If you aren’t familiar with the terminology in this section, please check the Glossary of Terms.

The mediation analysis for Hypotheses 7-10 in the original study was conducted using model 4 of Andrew Hayes’ PROCESS macro in SPSS. We used the same model in the R version (R Core Team, 2022) of PROCESS. Model 4 includes an independent variable, an outcome or dependent variable, and a mediator variable, which are illustrated below in the case of this experiment.

In the model used in this study and illustrated above, there is: 

• An independent variable (which can be categorical, as in this study), 
• A dependent variable, and
• A mediator variable (that mediates the relationship between the independent and the dependent variable)

These variables are shown below, along with the names that are traditionally given to the different “paths” in the model. 

In the diagram above…

• The “a” paths (from the independent variables to the mediator variable) are quantified by finding the coefficient of the independent variable in a linear regression predicting the mediator variable. 
• The “b” and “c’ ” paths are quantified by finding the coefficients of the mediator and independent variables (respectively) in a regression involving the dependent variable as the outcome variable and all other relevant variables (in this case: the independent variable and the mediator variable) as the predictor variables. 

In Hayes’ book, he states that mediation can be said to be occurring as long as the indirect effect – which is the multiple of the a and b coefficients – is different from zero. In other words, as long as the effect size of a*b (i.e, the path from the independent variable to the dependent variable via the mediator variable) is different from zero, the variable in the middle of the diagram above is said to be a significant mediator of the relationship between the independent and dependent variable. PROCESS uses bootstrapping (by default, with 10,000 resamples) to obtain an estimate of the lower and upper bound of the 95% confidence interval of the size of the ab path. If the confidence interval does not include 0, the indirect effect is said to be statistically significant. 

The original random seed (used by the original authors in SPSS) was not saved. We corresponded with Andrew Hayes (the creator of PROCESS) about this and have included notes from that correspondence in the Appendices. In our replication, we used a set seed to allow other teams to reproduce and/or replicate our results in R.

Mediation results in more detail

Like the original paper, we found that collective meaning was a statistically significant mediator (with 95% confidence intervals excluding 0) of the relationship between each experimental condition and perceived sacredness.  

In the table below, please note that “All conditions” refers to the mediation results when all experimental conditions were coded as “1”s and treated as the independent variable (with the control condition being coded as “0”).

Mediator: Collective Meaning	Original Results	Replication Results	Replicated?
Combined vs. Control (H7)	[0.06, 0.15]	[0.6035, 0.9017]	✅
Historical vs. Control (H8)	[0.06, 0.16]	[0.4643, 0.7171]	✅
Spiritual vs. Control (H9)	[0.26, 0.54]	[0.5603, 0.8298]	✅
All Conditions	[0.05, 0.11]	[0.5456, 0.7699]	✅

Mediation results for Hypothesis 10

For Hypothesis 10, the original study tested a variable as a potential mediator of the relationship between experimental condition and sacredness if there was a statistically significant difference in a particular variable across conditions when running the one-way ANOVAs. We followed the same procedure. See the notes on the mediation analysis plan in the appendices for more information about this.

When testing the alternative mediators of uniqueness and usefulness, the original study authors found that uniqueness was (and usefulness was not) a statistically significant mediator of the relationships between each of the experimental conditions and perceived sacredness. We replicated the results with respect to uniqueness, except in the case of the relationship between the spirituality condition and perceived sacredness, for which uniqueness was not a statistically significant mediator.

Insofar as we did not find that usefulness was a positive mediator of the relationship between experimental conditions and perceived sacredness, our results were consistent with the original study’s conceptual argument. However, unlike the original study authors, we found that usefulness was a statistically significant negative mediator (with an indirect effect significantly below zero) of the relationships between two of the experimental conditions (the historical condition and the combined condition) and perceived sacredness. 

Alternative Mediator: Uniqueness (H10)	Original Results	Replication Results	Replicated?
Combined vs. Control	[0.02, 0.06]	[0.1809, 0.3753]	✅
History vs. Control	[0.02, 0.10]	[0.1984, 0.3902]	✅
Spirituality vs. Control	[0.01, 0.13]	[-0.1082, 0.0705]	❌
All Conditions	[0.03, 0.07]	[0.1212, 0.2942]	✅

Alternative Mediator: Usefulness (H10)	Original Results	Replication Results	Replicated?
Combined vs. Control	[−.02, 0.01]	[-0.1216, -0.0128]	❌
History vs. Control	[−0.06, −0.01]	[-0.1689, -0.0549]	✅
Spirituality vs. Control	[−.02, 0.09]	[-0.0364, 0.0692]	✅
All Conditions	[−.02, 0.00]	[-0.0860, -0.0152]	❌

In our replication, unlike in the original study, the one-way ANOVAs revealed statistically significant differences across conditions with respect to: personal meaning (F(3, 1251) = 11.35, p = 2.40 E-7), positive emotions (F(3, 1251) = 7.13, p = 4.35E-3), and negative emotions (F(3, 1251) = 3.78, p = 0.01). 

As seen in the tables below, in each case, when we entered these alternative mediators, the variable was found to be a statistically significant mediator of the effect of all conditions (combined) on sacredness. Except for positive emotions, which wasn’t a statistically significant mediator of the effect of the spirituality condition (versus control) on sacredness, the listed variables were statistically significant mediators of the effects of all of the other experimental conditions (both combined and individually) on sacredness.

Alternative Mediator: Personal Meaning (H10)	Original Results	Replication Results
Combined vs. Control	Not tested due to non-significant ANOVA results for these variables	[-0.1216, -0.0128]
History vs. Control		[0.1605, 0.3995]
Spirituality vs. Control		[0.0787, 0.3144]
All Conditions		[0.1684, 0.3619]

There were 24 Buddhists in the sample. As in the original study, analyses were performed both with and without Buddhists in the sample, and the results without Buddhists were consistent with the results with them included. All findings that were statistically significant with the Buddhist included were also statistically significant (and with effects in the same direction) as the dataset with the Buddhists excluded, except for the fact that, when Buddhists were included in the sample (as in the tables above), usefulness did not mediate the relationship between the spiritual significance condition (versus control) and sacredness (95% confidence interval: [-0.0364, 0.0692]), whereas with the Buddhist-free dataset, usefulness was a statistically significant (and negative) mediator of that relationship (95% confidence interval: [-0.1732, -0.0546]).

Interpreting the results

Most of the findings in the original study were replicated in our study. However, our results diverged from the original paper’s results when it came to several of the subcomponents of Hypothesis 10. Some of the alternative mediators included in the original study questions weren’t entered into mediation analyses in the original paper because the ANOVAs had not demonstrated statistically significant differences in those variables across conditions. However, we found significant differences for all of these variables in the ANOVAs that we ran on the replication dataset, so we tested them in the mediation analyses. 

In the original study, uniqueness was a significant mediator of the relationship between experimental condition and perceived sacredness, which partially contradicted Hypothesis 10. In our replication study, not only was uniqueness a significant mediator of this relationship, but so was personal meaning,  negative emotions, and (except for the relationship between spiritual significance and sacredness) so were usefulness and positive emotions. Thus, our study contradicted most of the sub-hypotheses in Hypothesis 10. 

Despite the fact that multiple alternative mediators were found to be significant in this study, when these alternative mediators were included as covariates, collective meaning continued to be a significant mediator of the relationship between experimental condition and perceived sacredness. This means that even when alternative mediators are considered, the main finding (that collective meaning influences sacredness judgments) holds in both the original study and our replication.

We had concerns about the interpretation of the study results that are reflected only in the Clarity Rating. These revolve around (1) the manipulation of uniqueness and the way in which this was reported in the study and (2) the degree to which alternative explanations can be ruled out by the study’s design and the results table.

Manipulating Uniqueness

The control condition in the original study did not manipulate uniqueness in the way it was intended to manipulate it.

In the original study, the control condition was introduced for the following reason: 

“By manipulating how historic the artwork was [in our previous study], we may have inadvertently affected perceptions of how unique the artwork was, since old things are typically rare, and there may be an inherent link between scarcity and sacredness…to help ensure that collective transcendence beliefs, and not these alternative mechanisms, are driving our effects, in Study 4 we employed a more stringent control condition that …emphasized the uniqueness of the art without highlighting its historical significance or its importance to collective spirituality”

In other words, the original authors intended for uniqueness to be ruled out as an explanation for higher ratings of sacredness observed in the experimental conditions. Throughout their pre-registration, the authors referred to “a control condition manipulating the art’s uniqueness” as their point of comparison for both collective meaning and sacredness judgments of artwork across the different experimental conditions. 

Unfortunately, however, their control condition did not successfully induce perceptions of uniqueness in the way that the authors intended. The control condition was significantly less unique than each of the experimental conditions, whereas to serve the purpose it had been designed for, it should have been perceived to be at least as unique as the experimental conditions. 

Although the paper did mention this finding, it did not label it as a failed manipulation check for the control condition. We think this is one important area in which the paper could have been written more clearly. When introducing study 4, they emphasized the intention to rule out uniqueness as an explanation for the different sacredness ratings. In the discussion paragraph associated with study 4, they again talk about their findings as if they have ruled out the uniqueness of the artwork as an explanation. However, as explained above, the uniqueness of the artwork was not ruled out by the study design (nor by the study findings).

For clarity in this report and our pre-registration, we refer to the fourth condition as simply “a control condition.” In addition, in an attempt to address these concerns regarding the interpretation of the study’s findings, we included a fifth condition that sought to manipulate the uniqueness of the artwork in such a way that the perceived uniqueness of the artwork in that condition was at least as high on the Likert scale as the uniqueness of the artwork in the experimental conditions. Please note that this fifth condition was only considered in our assessment of the Clarity rating for the current paper, not the Replicability rating. Please see the appendix for the results related to this additional condition.

The paper’s discussion of alternative mediators

The claim that “Study 4’s design also helped rule out a number of alternative explanations” is easily misinterpreted. 

In the discussion following study 4, the original authors claim that:

“Study 4’s design also helped rule out a number of alternative explanations, including the uniqueness of the artwork, positivity and negativity felt toward the art, and the personal meaning of the work.”

The fact that this explanation includes the world “helped” is key – if the claim had been that the study design “definitively ruled out” alternative explanations, it would have been false. This is because, in the absence of support for the alternative mediators that were tested, the most one could say is that the experiment failed to support those explanations, but due to the nature of null hypothesis significance testing (NHST), those alternative explanations cannot be definitively “ruled out.” In order to estimate the probability of the null hypothesis directly, the paper would have needed to use Bayesian methods rather than only relying on frequentist methods. 

Especially in the context of NHST, it is not surprising that Hypothesis 10 was far less supported (i.e., more extensively contradicted) by our results than by the results of the original study, because of our larger sample size. The claim quoted above could be misinterpreted if readers under-emphasized the word “helped” or readers they focused on the idea of “ruling out” the mediators with null results.

Another way in which this part of the discussion of study 4 in the paper is less than optimally clear is in the discrepancy between the discussion and the mediation results table. Rather than showing the uniqueness of the artwork was not a likely explanation, the original paper only showed that it was not the only explanation. The authors recorded these findings in a table (Table 9 in the original paper), but the discussion did not discuss the implications of the finding in the table that uniqueness was also a significant mediator of the relationship between spiritual, historical, and combined historical and spiritual significance on the perceived sacredness of artwork. 

Interestingly, however, when we ran a mediation analysis on the original paper’s data, and entered uniqueness as a mediator, with collective meaning and usefulness as covariates, we found that uniqueness was, indeed, not a statistically significant mediator (using the same random seed as throughout this write-up, the 95% confidence interval included 0: [-0.0129, 0.0915]). This aligns with the claim in the discussion that the original study had not found evidence in favor of it being a mediator. However, such results do not appear to be included in the paper; instead, Table 9 in the original paper shows mediation results for each individual mediator variable on their own (without the other variables entered as covariates), and in that table, uniqueness is a significant mediator (which is contrary to what the discussion section implies).

Our study also replicated the finding that uniqueness was a significant mediator between experimental condition and perceived sacredness (when entered into the model without any covariates), except in the case of the spiritual condition versus control. Additionally, in our study, we found several more mediators that were statistically significant by the same standards of statistical significance used by the original authors (again, when entered into the model without any covariates). 

The overall claim that collective meaning remains a mediator above and beyond the other mediators considered in the study remained true when the other variables that appeared relevant (uniqueness and usefulness) were entered as covariates in the original study data. The claim was also true for our dataset, including when all the considered mediators were entered as covariates.

Conclusion

We replicated 90% of the results reported in study 4 from the paper, “Collective transcendence beliefs shape the sacredness of objects: the case of art.” The original study’s methods and data were mostly recorded and shared transparently, but the exclusion procedures were only partially shared and the related free-text data were not shared; there were also some minor deviations from the pre-registration. The original paper would have benefited from clearer explanations of the study’s results and implications. In particular, we suggest that it would have been preferable if the discussion section for study 4 in the original paper had acknowledged that the experiment had not controlled for uniqueness in the way that had been originally planned, and if the table of results and discussion had been consistent with each other. 

Acknowledgements

We would like to thank the team who ran the original study for generously reviewing our materials, sending us their original study materials, helping us to make this replication a faithful one, and providing helpful, timely feedback on our report. (As with all our reports, though, the responsibility for the contents of the report remains with the author and the rest of the Transparent Replications team.)

Many thanks to Amanda Metskas for her extensive involvement throughout the planning, running, and reporting of this replication study. Amanda had a central role in the observations we made about the original study’s control condition, and she also highlighted the subsequent necessity of including an alternative control condition in our study. Many thanks also go to Spencer Greenberg for his helpful feedback throughout, to our hypothesis-blinded coders, Alexandria Riley and Mike Riggs, for their help in excluding participants according to our exclusion protocol, and to our Ethics Evaluator. Thank you to the forecasters on Metaculus who engaged with our study description and made predictions about it. Last but certainly not least, many thanks to our participants for their time and attention.

Purpose of Transparent Replications by Clearer Thinking

Transparent Replications conducts replications and evaluates the transparency of randomly-selected, recently-published psychology papers in prestigious journals, with the overall aim of rewarding best practices and shifting incentives in social science toward more replicable research.

We welcome reader feedback on this report, and input on this project overall.

Appendices

Additional information about the pre-registration

In cases of discrepancies between a paper and a pre-registration, we take note of the differences, as this is relevant to the transparency of the paper, but we replicate what the authors described actually doing in the paper. 

There were differences between the pre-registered analysis plan and what was actually done (explained in the next section). In addition to this, there were subtle wording and formatting differences between the text in the pre-registration and the text used in the conditions in the actual study. Having said this, none of the wording discrepancies altered the meaning of the conditions. 

The pdf of the study questions that the team shared with us also included bold or underlined text in some questions, and these formatting settings were not mentioned in the pre-registration. However, we realize that bold or underlined text entered into the text fields of an OSF pre-registration template do not display as bold or underlined text when the pre-registration is saved. 

Additional information about the exclusion criteria

In preparation for replicating the process undertaken to implement exclusion criterion #3, we requested a copy of the written instructions given to the hypothesis-blinded coders in the original study. The original authorship team responded with the following: 

“I had a meeting/training session with my coders before letting them code everything. Like ask them to code 10% to see if they have high agreement, if not we discuss how to reach agreement. For example the response has to contain at least two critical informations about the artwork etc. so the instructions may vary depending on participants’ responses.” 

We wanted our exclusion procedures to be as replicable as possible, so instead of providing a training session, we provided a written guidelines document for our coders. See here for the guidelines document we provided to our coders. There was moderate agreement between the two hypothesis-blinded coders (ICC1 = 0.58, ICC2 = 0.59) and all disagreements were resolved by the first author.

Notes on corresponding with the original authors

There were some cases where the original authorship team’s advice was not consistent with what they had recorded in their pre-registration and/or paper (which we attributed to the fact that the study was conducted some time ago). In those cases, we adhered to the methods in the pre-registration and paper.

Full t-test results

Notes on Andrew Hayes’ PROCESS models

The original authorship team had used the PROCESS macro in SPSS and did not record a random seed. So the current author emailed Andrew Hayes about our replication and asked whether there is a default random seed that is used in SPSS, so that we could specify the same random seed in R. His response was as follows:

If the seed option is not used in the SPSS version, there is no way of recovering the seed for the random number generator. Internally, SPSS seeds it with a random number (probably based on the value of the internal clock) if the user doesn’t specify as seed.

SPSS and R use different random number generators so the same seed will produce different bootstrap samples. Since the user can change the random number generator, and the default random number generator varies across time, there really is no way of knowing for certain whether using the same seed will reproduce results. 

 Likewise, if you sort the data file rows differently than when the original analysis was conducted, the same seed will not reproduce the results because the resampling is performed at the level of the rows. This is true for all versions.

Notes on mediation analysis plans in the pre-registration

In their pre-registration, the authors had said: “We will also conduct this same series of mediation analyses for each of the alternative mediators described above. If any of the alternative mediators turn out to be significant, we will include these significant alternative mediators in a series of simultaneous mediation analyses (following the same steps as described above) entering them along with collective meaning.” In contrast, in their paper, they only reported on mediation analyses for the variables for which there were significant ANOVA results. And when they found a significant medicator, in the paper they described rerunning ANOVAs while controlling for those mediators, whereas in the pre-registration they had described rerunning mediation analyses with the additional variables as covariates.

Notes on the mediators considered in the original study design

In their set of considered explanations for the perceived sacredness of art, the authors considered the effects of (i) individual meaningfulness in addition to (ii) collective meaning, and they considered the effects of (i) individual positive emotions, but they did not consider the effects of (ii) collective positive emotions.

The original study authors included a question addressing the individual meaningfulness of the artwork, as they acknowledged that the finding about collective meaning was more noteworthy if it existed above and beyond the effects of individual meaningfulness. They also included a question addressing individual positive emotions so that they could examine the impact of this variable on sacredness. In the context of this study, it seems like another relevant question to include would relate to the effects of collective positive emotions (as the collective counterpart to the question about individual positive emotions). One might argue that this is somewhat relevant to the clarity of this paper: ideally, the authors would have explained the concepts in such a way as to make the inclusion of a question about collective positive emotions an obvious consideration.

We therefore included a question addressing collective positive emotions. (We did not include multiple questions, despite the fact that there were multiple questions addressing collective meaningfulness, because we wanted to minimize the degree to which we increased the length of the study.) The additional question was included as the very last question in our study, so that it had no impact on the assessment of the replicability of the original study (as the replication component was complete by the time participants reached the additional question). 

Results from extensions to the study

The t-test results table above includes a row of results (pertaining to the effect of collective positive emotions) that were outside the scope of the replication component of this project.

We also conducted an extra uniqueness versus control comparison which is somewhat relevant to the clarity rating of the study, but represents an extension to the study rather than a part of the replicability assessment.

Our newly-introduced, fifth condition was designed to be perceived as unique. It was rated as more unique than the original study’s control condition, and this difference was statistically significant (M_{new_condition} = 5.26; M_control = 4.87; student’s t-test: t(611) = 1.26 E-3; d = -0.26). It was also rated as more unique than the spiritual significance condition; however, it was rated as less unique than the individual historical significance condition and the combined historical and spiritual significance condition.

In addition to being rated as more unique than the original control, the fifth condition was also rated as more historically significant than the control condition, and this difference was also statistically significant. Having said this, the degree of perceived historical significance was still statistically significantly lower than the perceived historical significance in each of the (other) experimental conditions (M_{new_condition} = 3.52; M_control = 3.21; student’s t-test: t(611) = 0.02; d = -0.19).  

In summary, our results suggest that our fifth condition provides a more effective manipulation of the level of uniqueness of the artwork (in terms of its effect on uniqueness ratings) compared to the original control. However, the historically significant conditions were both still rated as more unique than the fifth condition. This means that the study design has been unable to eliminate differences in perceived uniqueness between the control and experimental conditions. Since more than one variable is varying across the conditions in the study, it is difficult to draw definitive conclusions from this study. It would be premature to say that uniqueness is not contributing to the differences in perceived sacredness observed between conditions.

So, once again, like the original authors, we did not have a condition in the experiment that completely isolated the effects of collective meaning because our control condition did not serve its purpose (it was meant to have the same level of uniqueness as the experimental conditions while lacking in historical and spiritual significance, but instead it had a lower level of perceived uniqueness than two of the other conditions, and it was rated as more historically significant than the original control).

If future studies sought to isolate the effects of collective meaning as distinct from uniqueness, teams might want to give consideration to instead trying to reduce the uniqueness of an already spiritually meaningful or historically significant artwork, by having some conditions in which the artwork was described as one of many copies (for example), so that comparisons could be made across conditions that have different levels of uniqueness but identical levels of historical and spiritual meaningfulness. This might be preferable to trying to create a scenario with a unique artwork that lacks at least historical significance (potentially as a direct consequence of its uniqueness). 

The table below provides t-test results pertaining to our replication dataset, comparing the control condition with the alternative control condition that we developed.

Replication Analysis Extension	Control n = 294	Alternative control n = 319
Variable	Mean (Stnd Dev.)	Mean (Stnd Dev.)	t value	p	Cohen’s d
Historical significance	3.21 (1.64)	3.52 (1.55)	2.4	0.02	0.19
Collective spirituality	3.97 (1.55)	4.16 (1.48)	1.56	0.12	0.13
Uniqueness	4.87 (1.57)	5.26 (1.38)	3.24	1.26e -3	0.26
Sacredness	3.08 (1.16)	3.36 (1.30)	2.79	5.49e -3	0.23
Personal meaning	2.96 (1.58)	3.03 (1.51)	0.55	0.58	0.04
Collective meaning	4.19 (1.45)	4.50 (1.37)	2.75	6.20e -3	0.22
Usefulness	3.90 (1.61)	3.50 (1.61)	-3.09	2.08e -3	-0.25
Positive emotions	5.13 (1.31)	5.09 (1.18)	-0.41	0.68	-0.03
Collective positive emotions	5.00 (1.24)	4.99 (1.07)	0.1	0.92	7.91e -3
Negative emotions	1.95 (1.18)	1.92 (1.14)	0.26	0.8	0.02

In addition to investigating an alternative control condition, we included one additional potential mediator: collective positive emotions. The reasoning for this was explained above. Our results suggest that perceived collective positive emotions could also mediate the relationship between experimental conditions and the perceived sacredness of artwork. It may be difficult to disentangle the effects of collective meaning and collective positive emotions, since both of these varied significantly across experimental conditions and since there was a moderate positive correlation between them (Pearson’s r = 0.59).

The additional variable that we collected, perceived collective positive emotions, was a statistically significant mediator of the relationship between all of the experimental conditions and perceived sacredness.

Alternative Mediator: Collective Positive Emotions (extension to H10)	Results
Combined vs. Control	[0.2172, 0.4374]
History vs. Control	[0.1402, 0.3476]
Spirituality vs. Control	[0.1765, 0.3795]
All Conditions	[0.2068, 0.3897]

Glossary of terms

Please skip this section if you are already familiar with the terms. If this is the first time you are reading about any of these concepts, please note that the definitions given are (sometimes over-)simplifications.

• Independent variable (a.k.a. predictor variable): a variable in an experiment or study that is altered or measured, and which affects other (dependent) variables. [In many studies, including this one, we don’t know whether an independent variable is actually influencing the dependent variables, so calling it a “predictor” variable may not be warranted, but many models implicitly assume that this is the case. The term “predictor” variable is used here because it may be more familiar to readers.] 
• Dependent variable (a.k.a. outcome variable): a variable that is influenced by an independent variable. [In many studies, including this one, we don’t know whether a dependent variable is actually being causally influenced by the independent variables, but many models implicitly assume that this is the case.] 
• Null Hypothesis: in studies investigating the possibility of a relationship between given pairs/sets of variables, the Null Hypothesis assumes that there is no relationship between those variables.
• P-values: the p-value of a result quantifies the probability that a result at least as extreme as that result would have been observed if the Null Hypothesis were true. All p-values fall in the range (0, 1].
• Statistical significance: by convention, a result is deemed to be statistically significant if the p-value is below 0.05, meaning that there is a 5% chance that a result at least as extreme as that result would have occurred if the Null Hypothesis were true.
  • The more statistical tests conducted in a particular study, the more likely it is that some results will be statistically significant due to chance. So, when multiple statistical tests are performed in the same study, many argue that one should correct for multiple comparisons.
  • Statistical significance also does not necessarily translate into real-world/clinical/practical significance – to evaluate that, you need to know about the effect size as well.
• Linear regression: this is a process for predicting levels of a dependent/outcome variable (often called a y variable) based on different levels of an independent/predictor variable (often called an x variable), using an equation of the form y = mx + c (where m is the rate at which the dependent/outcome variable changes as a function of changes in the independent/predictor variable, and c describes the level of the dependent variable that would be expected if the independent/predictor variable, x, was set to a level of 0).
• Mediator variable: a variable which (at least partly) explains the relationship between a predictor variable and an outcome variable. [Definitions of moderation vary, but Andrew Hayes defines it as occurring any time when an indirect effect – i.e., the effect of a predictor variable on the outcome variable via the mediator variable, is statistically significantly different from zero.]
• Moderator variable: a variable which changes the strength or direction of a relationship between a predictor variable and an outcome variable. 
• Categorical variables: these are variables described in terms of categories (as opposed to being described in terms of a continuous scale).

References

Chen, S., Ruttan, R. L., & Feinberg, M. (2022). Collective transcendence beliefs shape the sacredness of objects: The case of art. Journal of Personality and Social Psychology. 124(3), 521–543. https://doi.org/10.1037/pspa0000319 

Faul, F., Erdfelder, E., Buchner, A., & Lang, A.-G. (2009). Statistical power analyses using G*Power 3.1: Tests for correlation and regression analyses. Behavior Research Methods, 41, 1149-1160. Download PDF

Hayes, A. F. (2022). Introduction to mediation, moderation, and conditional process analysis a regression-based approach (Third edition). The Guilford Press.

JASP Team (2020). JASP (Version 0.14.1 ) [Computer software].

JASP Team (2023). JASP (Version 0.17.3) [Computer software].

R Core Team (2022). R: A language and environment for statistical computing. R Foundation for
Statistical Computing, Vienna, Austria. URL https://www.R-project.org/.

Executive Summary

Transparency	Replicability	Clarity
	1 of 1 findings replicated

We ran a replication of study 1 from this paper, which found that the variety in a person’s social interactions predicts greater well-being, even when controlling for their amount of in-person social interaction.  This finding was replicated in our study. 

In this study participants were asked about their well-being over the last 24 hours, and then asked about their activities the previous day, including how many in-person interactions they had, and the kinds of relationships they have with the people in those interactions (e.g. spouse or partner, other family, friends, coworkers, etc.). The variety of interactions, called “social portfolio diversity,” had a positive association with well-being, above and beyond the positive effects due to the amount of social interaction.

Although this finding replicated, this paper has serious weaknesses in transparency and clarity. The pre-registered hypothesis differed from the hypothesis tested, and the authors do not acknowledge this in the paper. The main independent variable, social portfolio diversity, is described as being calculated in three conflicting ways in different parts of the paper and in the pre-registration. The findings reported in the paper are based on what we believe to be incorrect calculations of their primary independent and control variables (i.e., calculations that contradict the variable definitions given in the paper), and their paper misreports the sample size for their main analysis because the calculation error in the primary independent variable removed 76 cases from their analysis. Unfortunately, the authors did not respond to emails seeking clarification about their analysis.

Despite the flaws in the analysis, when these flaws were corrected, we found that we were indeed able to replicate the original claims of the paper – so the main hypothesis itself held up to scrutiny, despite inconsistencies and seeming mistakes with how calculations were performed.

(Update: On 8/9/2023 the authors wrote to us that they will be requesting that the journal update their article with a clarification.)

Full Report

Study Diagram

Replication Conducted

We ran a replication of Study 1 from: Collins, H.K., Hagerty, S.F., Quiodbach, J., Norton, M.I., & Brooks, A.W. (2022). Relational diversity in social portfolios predicts well-being. Proceedings of the National Academy of Sciences, 119(43), e2120668119. https://doi.org/10.1073/pnas.2120668119

How to cite this replication report: Transparent Replications by Clearer Thinking. (2023). Report #5: Replication of a study from “Relational diversity in social portfolios predicts well-being” (PNAS | Collins et al. 2022) https://replications.clearerthinking.org/replication-2022pnas119-43
(Preprint DOI: https://doi.org/10.31234/osf.io/jfmsz)

Key Links

• Our Research Box for this replication report includes the pre-registration, study materials, de-identified data, and analysis files.
• Manifold Markets predicted a 52% probability of this study replicating.
• Metaculus predicted a 62% probability of this study replicating.
• Download a PDF of the original paper.
• The supporting materials for the original paper can be found on OSF.

Overall Ratings

To what degree was the original study transparent, replicable, and clear?

Transparency:  how transparent was the original study?	This study provided data and experimental materials through OSF, which were strong points in its transparency. Analysis transparency was a weakness, as no analysis code was provided, and the authors did not respond to inquiries about a key analysis question that was left unanswered in the paper and supplemental materials. The study was pre-registered; however, the authors inaccurately claimed that their main hypothesis was pre-registered, when the pre-registered hypothesis did not include their control variable.
Replicability: to what extent were we able to replicate the findings of the original study?	The main finding of this study replicated when the control variable was calculated the way the authors described calculating it, but not when the control variable was calculated the way the authors actually did calculate it in the original paper. Despite this issue, we award the study 5 stars for replication because their key finding met the criteria for replication that we outlined in our pre-registration.
Clarity: how unlikely is it that the study will be misinterpreted?	Although the analysis used in this study is simple, and reasonable, there are several areas where the clarity in this study could be improved. The study does not report an R2 value for its regression analyses, which obscures the small amount of the variance in the dependent variable that is explained by their overall model and by their independent variable specifically. Additionally, the computation of the key independent variable is described inconsistently, and is conducted in a way that seems to be incorrect in an important respect. The sample size reported in the paper for the study is incorrect due to excluded cases based on the miscalculation of the key independent variable. The calculation of the control variable is not conducted the way it is described in the paper, and appears to be miscalculated. (Update: On 8/9/2023 the authors wrote to us that they will be requesting that the journal update their article with a clarification.)

Detailed Transparency Ratings

Overall Transparency Rating:
1. Methods Transparency:	A pdf showing the study as participants saw it was available on OSF.
2. Analysis Transparency:	Analysis code was not available and authors did not respond to emails asking questions about the analysis. A significant decision about how a variable is calculated was not clear from the paper, and we did not get an answer when we asked. Descriptions of how variables were calculated in the text of the paper and pre-registration were inconsistent with each other and inconsistent with what was actually done.
3. Data availability:	Data were available on OSF.
4. Pre-registration:	The study was pre-registered; however, the pre-registered hypothesis did not include the control variable that was used in the main analysis reported in the paper. The text of the paper stated that the pre-registered hypothesis included this control variable. The pre-registered uncontrolled analysis was also conducted by the authors, but the result was only reported in the supplementals and not the paper itself, and is not presented as a main result. Additionally, the pre-registration incorrectly describes the calculation method for the key independent variable.

Summary of Study and Results

Both the original study (N = 578) and our replication study (N = 961) examined whether the diversity of relationship types represented in someone’s in-person interactions in a given day predicts greater self-reported well-being the next day, beyond the effect of the total amount of in-person interaction in that day.

In the experiment, participants filled out a diary about their activities on the previous day, reporting 3 to 9 episodes from their day. For each episode they reported, participants were then asked about whether they were interacting with anyone in person, were interacting with anyone virtually, or were alone. For episodes where people reported in-person interactions, they were asked to check all of the checkboxes indicating the relationship types they had with the people in the interaction. The options were: spouse/significant other, adult children, young children or grandchildren, family (other than spouse/child), friends, co-workers, and other people not listed.

For each participant, we calculated their “social portfolio diversity” using the equation on p. 2 of the original study. More information about the computation of this variable is in the detailed results section. There were 971 participants who completed the study. We excluded 6 participants who failed the attention check from the data analysis, and 4 due to data quality issues, leaving N = 961. More details about the data exclusions is available in the appendix.

The dataset was analyzed using linear regression. The main analysis included social portfolio diversity as the main independent variable, the proportion of activities reported in the day that included in-person social interaction as a control variable, and the average of the two well-being questions as the dependent variable. The original study reported a statistically significant positive relationship between the social portfolio diversity variable and well-being in this analysis (β = 0.13, b = 0.54, 95% CI [0.15, 0.92], P = 0.007, n = 576), but please see the detailed results section for clarifications and corrections to these reported results. 

In our replication, we found that this result replicated both when the social portfolio diversity variable was calculated as 0 for subjects with no reported in-person interactions (β = 0.095, b = 0.410, 95% CI [0.085, 0.735], P = 0.014, n = 961) and when the 116 subjects with no in-person interactions reported are dropped due to calculating their social portfolio diversity as “NaN”  (β = 0.097, b = 0.407, 95% CI [0.089, 0.725], P = 0.012, n = 845). Note that calculating the control variable the way the original authors calculated it in their dataset, rather than the way they described it in the paper, resulted in non-significant results. Based on our pre-registered plan to calculate that variable the way it is described in the paper, we conclude that their main finding replicated. We are nonetheless concerned about the sensitivity of this finding to this small change in calculating the control variable.

Detailed Results

Computing the Social Portfolio Diversity and Amount of Social Interaction variables

(Update: On 8/9/2023 the authors wrote to us that they will be requesting that the journal update their article with a clarification.)

The “social portfolio diversity” equation is how the authors construct their primary independent variable. This equation involves computing, for each of the relationship categories a person reported having interactions with, the proportion of their total interactions that this category represented (which the authors call “p_i”). For each category of relationship, this proportion is multiplied by its natural logarithm. Finally, all these products are summed together and multiplied by negative one so the result is a positive number. The original authors chose this formula in order to make the “social portfolio diversity” variable resemble Shannon’s biodiversity index. 

How is p_i calculated in the Social Portfolio Diversity variable?

The computation of the “social portfolio diversity” variable is described by the authors  in three conflicting ways. From analyzing the data from their original study (as described in the section below on reproducing the original results), we were able to determine how this variable was actually calculated.

In the original paper the authors describe the calculation of the formula as follows:

where s represents the total number of relationship categories (e.g., family member, coworker, close friend, stranger) an individual has reported interacting with, and p_i represents the proportion of total interactions (or proportion of total amount of time spent interacting) reported by a participant that falls into the ith relationship category (out of s total relationship categories reported). The diversity measure captures the number of relationship categories that an individual has interacted with (richness) as well as the relative abundance of interactions (or amount of time spent interacting) across the different relationship categories that make up an individual’s social portfolio (evenness) over a certain time period (e.g., yesterday). We multiply this value by -1, so higher portfolio diversity values represent a more diverse set of interaction partners across relationship categories (see Fig. 1).  [italicized and bolded for emphasis]

This description explains how the authors calculated the p_i variable. It’s important to note that here the “proportion of total interactions” is calculated by using the sum of the number of interaction types checked off for each episode, not the total number of episodes of in-person interaction. For example, if a person reported 3 episodes of their day with in-person interactions, and in all 3 they interacted with their spouse, and in 2 of those they also interacted with their kids, the p_i for spouse interactions is 3/5, because they had 3 spouse interactions out of 5 total interactions (the spouse interactions plus the child interactions), not 3 spouse interactions out of 3 total episodes with in-person interactions in the day. The description of how this variable is calculated in the “Materials and Methods” section of the paper describes this variable as being constructed using the second of these two methods rather than the first.  Here is that text from the paper:

Social portfolio diversity was calculated as follows: 1) dividing the number of episodes yesterday for which an individual reported interacting with someone in a specific social category by the total number of episodes they reported interacting with someone in any of the categories, giving us p_i; 2) multiplying this proportion by its natural log (p_i × ln p_i); 3) repeating this for each of the seven social categories; and 4) summing all of the (p_i × ln p_i) products and multiplying the total by -1. [italicized and bolded for emphasis]

In the pre-registration the calculation of this variable is described as:

From these questions, we will calculate our primary DV: Convodiversity

To calculate convodiversity, we will:

• Divide the number of times an individual interacted with someone in a certain social category in a day (e.g., spouse, friend, coworker) by the total number of people they interacted with that day, which gives us p_i.

• Multiply this proportion by its natural log (p_i X ln p_i).

• Repeat this for each specific social category assessed, and

• Sum all of the (p_i X ln p_i) products and multiple the total by -1.

This would be yet a third possible way of calculating p_i, which would result in 3 spouse interactions out of 2 people interacted with in the day for the example above.

It seems like the way that p_i was actually calculated is more likely to be both correct and consistent with the author’s intent than the other two possible ways they describe calculating p_i. We calculated Social Portfolio Diversity consistently with the way they actually calculated it for our analyses. Note that our experiment was coded to compute the Social Portfolio Diversity variable automatically during data collection, but this code was calculating the variable the way the authors described in the “Materials and Methods” section of their paper, prior to us noticing the inconsistency. We did not use this variable, and instead re-constructed the Social Portfolio Diversity variable consistently with the authors’ actual method.

How are people with no in-person episodes handled by the Social Portfolio Diversity equation?

The other problem we ran into in the calculation of the social portfolio diversity variable is what should be done when participants have 0 in-person social interactions reported for the day. Looking at the description of how the variable is calculated and the summation notation, it seems like in this case s, the total relationship categories reported, would be 0. This causes the equation to contain the empty sum, which resolves to 0, making the entire Social Portfolio Diversity equation for participants with no in-person social interactions resolve to 0.

That is not how the equation was resolved in the data analysis in the original paper. In the dataset released by the authors, the participants with no in-person social interactions reported for the day, have a value of “NaN” (meaning Not a Number) given for the Social Portfolio Diversity variable, and in the analyses that include that variable, these participants are excluded for having a missing value on this variable.

Because we did not hear back from the authors when we reached out to them about their intentions with this calculation, we decided to run the analysis with this variable computed both ways, and we pre-registered that plan.

How is the control variable calculated?

When we re-analyzed the authors’ original data, we used the perc_time_social variable that they included in their dataset as their control variable representing the total amount of in-person interaction in the day. Using that variable resulted in reproducing the authors’ reported results on their data; however, after doing that re-analysis, it later became clear that the “perc_time_social” variable that the authors computed was not computed the way they described in their paper. We were not aware of this issue at the time of filing our pre-registration, and we pre-registered that we would calculate this variable the way it was described in the paper, as “the proportion of episodes that participants spent socializing yesterday.” We interpreted this to mean the number of episodes involving in-person interactions out of the total number of episodes that the participant reported for their day. For example, imagine that a participant reported 9 total episodes for their day, and 7 of those episodes involved in-person interaction. This would result in a proportion of  7/9 for this variable, regardless of how many types of people were present at each episode involving in-person interaction.

When we examined the authors’ dataset more closely it became clear that their perc_time_social variable was not calculated that way. This variable was actually calculated by using the total number of interaction types for each episode added together, rather than the total episodes with in-person interaction, as the numerator. This is the same number that would be the denominator in the p_i calculation for the Social Portfolio Diversity variable. They then constructed the denominator by adding to that numerator 1 for each episode of the day that was reported that didn’t include in-person interactions. If we return to the example above, imagine that in the 7 episodes with in-person interaction, the participant reported interacting with their friends in 3, their spouse in 5, and their coworkers in 2. That would make the numerator of this proportion 10, and then for the denominator we’d add 2 for the two episodes with no in-person interaction, resulting in 10/12 as the proportion for this variable.

It is possible that this is what the authors actually intended for this variable, despite the description of it in the paper, because in the introduction to the paper they also describe this as controlling for the “total number of social interactions,” which could mean that they are thinking of this dyadically, rather than as episodes. This seems unlikely though, because calculating it this way incorporates aspects of social portfolio diversity into their control variable. It’s also a strange proportion to use because a single episode of in-person interaction could count for up to 7 in this equation, depending on the number of interaction types in them, while an episode without in-person interaction can only count as 1. The control variable seems intended to account for the amount of the day spent having in-person interactions, regardless of the particular people who were present. This is accomplished more simply and effectively by looking at the proportion of episodes, rather than incorporating the interaction types into this variable.

Despite this issue, these two methods of calculating this variable are highly correlated with each other (Pearson’s r = 0.96, p < .001 in their original data, and Pearson’s r = 0.989, p < .001 in our replication dataset). 

Reproducing the original results

Due to the original dataset evaluating participants with no reported in-person interactions as “NaN” for the Social Portfolio Diversity variable, it appears that the N the authors report for their Model 1 and Model 3 regressions is incorrect. They report an N of 577 for Model 1 and 576 for Model 3. The actual N for Models 1 and 3, with the cases with an “NaN” for Socal Portfolio Diversity excluded, is 500.

In their dataset of N = 578, their variable “ConvoDiv” (their Social Portfolio Diversity variable) is given as “NaN” in 78 cases. The regression results that are most consistent with the results they report are the results from N = 500 participants where “ConvoDiv” is reported as a number. If we modify their dataset and assign a 0 to the “ConvoDiv” variable for the 76 cases where a participant completed the survey but had no in-person social interaction the previous day, we get results that differ somewhat from their reported results. See the table below to see their reported results, and our two attempts to reproduce their results from their data. We attempted to clarify this by reaching out to the authors, but they did not respond to our inquiries.

	Reported results	Reproduced results	Reanalyzed results
	From Table S1 in the supplemental materials	Social Portfolio Diversity set to NA for people with no in-person episodes	Social Portfolio Diversity set to 0 for people with no in-person episodes
Model 1 Soc. Portfolio Div. only (IV only no control)	N = 577 Soc. Portfolio Div. β = 0.21, b = 0.84, 95%CI[0.50, 1.17] p < .001 R2 not reported	N = 500 Soc. Portfolio Div. β = 0.216, b = 0.835, 95%CI[0.504, 1.167] p < .001 R2 = 0.047 Adj. R2 = 0.045	N = 576 Soc. Portfolio Div. β = 0.241, b = 0.966, 95%CI[0.647, 1.285] p < .001 R2 = 0.058 Adj. R2 = 0.056
Model 3 Both Soc. Portfolio Div. (IV) and Prop. Inter. Social (control)	N = 576 Soc. Portfolio Div. β = 0.13, b = 0.54, 95%CI[0.15, 0.92] p = .007 Prop. Inter. Social β = 0.17, b = 0.99, 95%CI[0.32, 1.66] p = .004 R2 not reported	N = 500 Soc. Portfolio Div. β = 0.139, b = 0.537, 95%CI[0.150, 0.923] p = .007 Prop. Inter. Social β = 0.148, b = 0.992, 95%CI[0.321, 1.663] p = .004 R2 = 0.063 Adj. R2 = 0.059	N = 576 Soc. Portfolio Div. β = 0.133, b = 0.534, 95%CI[0.140, 0.927] p = .008 Prop. Inter. Social β = 0.180, b = 1.053, 95%CI[0.480,1.626] p < .001 R2 = 0.079 Adj. R2 = 0.076

Fortunately, the differences in the results between the two methods are small, and both methods result in a significant positive effect of Social Portfolio Diversity on well-being. We decided to analyze the data for our replication using both approaches to calculating the Social Portfolio Diversity variable because we wanted to both replicate exactly what the authors did to achieve the results they reported in their paper, and we also wanted to resolve the equation in the way we believe the authors intended to evaluate it (due to the equation they gave for social portfolio diversity and due to their reported N = 576). 

After determining that their calculation of the perc_time_social variable wasn’t as they described in the paper, and may not have been what they intended, we re-computed that variable as they described it, and re-ran their analyses on their data with that change (column 3 in the table below).

	Reported results	Reproduced results	Reanalyzed results
	From Table S1 in supplemental materials	using perc_time_social variable from original dataset	using proportion in-person episodes out of total episodes
Model 2 Control only	N = 576 Prop. Inter. Social β = 0.26, b = 1.53, 95%CI[1.07, 1.99] p < .001 R2 not reported	N = 577 perc_time_social β = 0.262, b = 1.528, 95%CI[1.068, 1.989] p < .001 R2 = 0.069 Adj. R2 = 0.067	N = 578 Prop. epi. In-person β = 0.241, b = 1.493, 95%CI[1.000, 1.985] p < .001 R2 = 0.058 Adj. R2 = 0.056
Model 3 IV & Control IV – NA for no interaction	N = 576 Soc. Portfolio Div. β = 0.13, b = 0.54, 95%CI[0.15, 0.92] p = .007 Prop. Inter. Social β = 0.17, b = 0.99, 95%CI[0.32, 1.66] p = .004 R2 not reported	N = 500 Soc. Portfolio Div. β = 0.139, b = 0.537, 95%CI[0.150, 0.923] p = .007 perc_time_social β = 0.148, b = 0.992, 95%CI[0.321, 1.663] p = .004 R2 = 0.063 Adj. R2 = 0.059	N = 500 Soc. Portfolio Div. β = 0.157, b = 0.606, 95%CI[0.234, 0.978] p = .001 Prop. ep. in-person β = 0.129 b = 0.89, 95%CI[0.223,1.558] p = .009 R2 = 0.060 Adj. R2 = 0.056
Model 3 IV & Control IV – 0 for no interaction		N = 576 Social Portfolio Div. β = 0.133, b = 0.534, 95%CI[0.140, 0.927] p = .008 perc_time_social β = 0.180, b = 1.053 95%CI[0.480,1.626] p < .001 R2 = 0.079 Adj. R2 = 0.076	N = 578 Social Portfolio Div. β = 0.152, b = 0.610, 95%CI[0.229, 0.990] p = .002 Prop. ep. In-person β = 0.157, b = 0.972, 95%CI[0.384,1.559] p = .001 R2 = 0.074 Adj. R2 = 0.071

We found that the coefficients for Social Portfolio Diversity are slightly stronger with the control variable calculated as the proportion of episodes reported that involve in-person interaction. In Model 2, using only the control variable, we found that when calculated as the proportion of episodes reported that involve in-person interaction the control variable explains slightly less of the variance than when it is calculated the way the authors calculated it. The R² for that model with the re-calculated control variable is 0.058. It was 0.069 using the perc_time_social variable as calculated by the authors.

We included the analysis files and data for these reanalyses in our Research Box for this report. The codebook for the data files marks variables that we constructed as “Added.” The other columns are from the dataset made available by the authors on OSF.

Our Replication Results

We  analyzed the replication data using both methods for calculating Social Portfolio Diversity, as discussed in our pre-registration. We also analyzed the data using both the way the control variable was described as being calculated (the way we said we would calculate it in our pre-registration), and the way the authors’ actually calculated it. We did this both ways because we wanted to conduct the study as we said we would in our pre-registration, which was consistent with how we believed the authors conducted it from the paper, and we also wanted to be able to compare their reported results to comparable results using the same variable calculations as the ones they actually did.

As with the original results, the two methods of calculating social portfolio diversity (dropping those people with no in-person social interactions or recording those participants as having a social portfolio diversity of zero) did not make a substantive difference in our results.

Unlike the original results, we found that there was a substantive difference in the results depending on how the control variable was calculated. When the control variable is calculated the way the authors calculated it in their original analyses, we find that the results do not replicate. When the control variable is calculated as the authors described in the paper (and how we pre-registered), we find that their results replicate. This difference held for both methods of calculating the social portfolio diversity variable. 

This was surprising given that the two versions of the control variable were correlated with each other at r = 0.989 in our data.  

Model 3 results using proportion of episodes as control variable

	Reanalyzed original results	Replication results
Model 3 IV & Control IV – NA for no interaction Control – Prop. episodes in-person	N = 500 Social Portfolio Div. β = 0.157, b = 0.606, 95%CI[0.234, 0.978] p = .001 Prop. ep. in-person β = 0.129, b = 0.89, 95%CI[0.223,1.558] p = .009 R2 = 0.060 Adj. R2 = 0.056	N = 845 Social Portfolio Div. β = 0.097, b = 0.407, 95%CI[0.089, 0.725] p = .012 Prop. ep. in-person β = 0.228, b = 1.556, 95%CI[1.042, 2.070] p < .001 R2 = 0.084 Adj. R2 = 0.082	✅
Model 3 IV & Control IV – 0 for no interaction Control – Prop. episodes in-person	N = 578 Social Portfolio Div. β = 0.152, b = 0.610, 95%CI[0.229, 0.990] p = .002 Prop. ep. in-person β = 0.157, b = 0.972, 95%CI[0.384,1.559] p = .001 R2 = 0.074 Adj. R2 = 0.071	N = 961 Social Portfolio Div. β = 0.095, b = 0.410, 95%CI[0.085, 0.725] p = .014 Prop. ep. in-person β = 0.263, b = 1.617, 95%CI[1.154, 2.080] p < .001 R2 = 0.108 Adj. R2 = 0.106	✅

Model 3 results using proportion of interactions as in original analysis as control variable

	Reanalyzed original results	Replication results
Model 3 IV & Control IV – NA for no interaction Control – perc_time _social as in original paper	N = 500 Social Portfolio Div. β = 0.139, b = 0.537, 95%CI[0.150, 0.923] p = .007 perc_time_social β = 0.148, b = 0.992, 95%CI[0.321, 1.663] p = .004 R2 = 0.063 Adj. R2 = 0.059	N = 845 Social Portfolio Div. β = 0.057, b = 0.242, 95%CI[-0.102, 0.586] p = .168 propSocialAsInOrigPaper β = 0.256, b = 1.691, 95%CI[1.151,2.231] p < .001 R2 = 0.087 Adj. R2 = 0.085	❌
Model 3 IV & Control IV – 0 for no interaction Control – perc_time _social as in original paper	N = 576 Social Portfolio Div. β = 0.133, b = 0.534, 95%CI[0.140, 0.927] p = .008 perc_time_social β = 0.180, b = 1.053, 95%CI[0.480,1.626] p < .001 R2 = 0.079 Adj. R2 = 0.076	N = 961 Social Portfolio Div. β = 0.055, b = 0.240, 95%CI[-0.112, 0.592], p = .182 propSocialAsInOrigPaper β = 0.292, b = 1.724, 95%CI[1.244, 2.205],  p < .001 R2 = 0.111 Adj. R2 = 0.109	❌

Due to the fact that we pre-registered calculating the control variable as “the number of episodes that involved in-person interaction over the total number of episodes the participant reported on,” and that we believe that this is a more sound method for calculating this variable, and it is consistent with how the authors described the variable in the text of their paper, we consider the main finding of this paper to have replicated, despite the fact that this is not the case if the control variable is calculated the way the authors actually calculated it in their reported results. Results for the Model 1 and Model 2 regressions are available in the appendix, as they were not the main findings on which replication of this study was evaluated.

Interpreting the Results

Despite the fact that these results replicated, we would urge caution in the interpretation of the results of this study. It is concerning that a small change in the calculation of the control variable to the method actually used by the authors in their original data analysis is enough to make the main finding no longer replicate. Additionally, the change in model R² accounted for by the addition of the social portfolio diversity variable to a model containing the control variable is very small (in our replication data the change in R² is 0.006 or 0.007 depending on how the social portfolio diversity variable is calculated). As mentioned earlier, the authors did not report the model R² anywhere in their paper or supplementary materials. 

Conclusion

The errors and inconsistencies in the computation and reporting of the results were a major concern for us in evaluating this study, and resulted in a low clarity rating, despite the simplicity and appropriateness of the analysis that was described in the paper. The claim in the paper that the main hypothesis was pre-registered, when the pre-registered hypothesis was different than what was reported in the paper, and the lack of response from the authors to emails requesting clarification about their social portfolio diversity variable, reduced the transparency rating we were able to give this study, despite the publicly accessible experimental materials and data. Despite these issues, we did find that the main finding replicated. 

(Update: On 8/9/2023 the authors wrote to us that they will be requesting that the journal update their article with a clarification.)

Acknowledgements

We are grateful to the authors for making their study materials and data available so that this replication could be conducted.

We provided a draft copy of this report to the authors for review on June 22, 2023. 

Thank you to Clare Harris at Transparent Replications who provided valuable feedback on this replication and report throughout the process. We appreciate the people who made predictions about the results of this study on Manifold Markets and on Metaculus. Thank you to the Ethics Evaluator for their review, and to the participants for their time and attention.

Purpose of Transparent Replications by Clearer Thinking

Transparent Replications conducts replications and evaluates the transparency of randomly-selected, recently-published psychology papers in prestigious journals, with the overall aim of rewarding best practices and shifting incentives in social science toward more replicable research.

We welcome reader feedback on this report, and input on this project overall.

Appendices

Additional Information about the Methods

Exclusion Criteria

We collected 971 complete responses to this study, and analyzed data from 961 subjects. The following table explains our data inclusion and exclusion choices.

Category	Number of Subjects	Excluded or Included	Reason
Attention Check	6	Excluded	Responded incorrectly to the attention check question by checking boxes other than “None of the above”
Attention Check	7	Included	Did not check any boxes in response to the attention check question. One subject reported in feedback on the study that they were not sure if they were supposed to select the option labeled “None of the above” for the attention check, or not select any of the checkboxes. Reanalyzing the data with these 7 subjects excluded does not change the results in any substantive way. These subjects are marked with a 1 in the column labeled AttnCheckLeftBlank.
Data Quality	2	Excluded	A visual inspection of the diary entries revealed two subjects who entered random numbers for their episode descriptions, and spent less than 2 minutes completing the study. All other subjects provided episode descriptions in words that were prima facia plausible. These two subjects were excluded due to a high likelihood that their responses were low quality, despite them passing the attention check question.
Data Quality	2	Excluded	Due to inconsistencies created when subjects edited diary entries, 2 subjects reported more than 9 episodes for the day. Reducing those episodes to the maximum of 9 would have required making decisions about whether to eliminate episodes involving in-person interaction or episodes not involving interaction, which would have impacted the results, therefore these two subjects’ responses were excluded.
Data Quality	10	Included	Due to inconsistencies created when subjects entered or edited their diary entries, 10 subjects’ numbers reported for total episodes or for in-person episodes were incorrect. These subjects’ data were able to be corrected using the saved diary information, without the need to make judgment calls that would impact the results, therefore these subjects’ data were included in the analysis. Reanalyzing the data with these 10 subjects excluded does not change the results in any substantive way. These subjects are marked with a 1 in the column labeled Corrected.

Additional information about the results

Model 1 results comparing original data and replication data

	Reanalyzed Original Results	Replication Results
Model 1 IV only IV – NA for no interaction	N = 500 Social Portfolio Div. β = 0.216, b = 0.835, 95%CI[0.504, 1.167] p < .001 R2 = 0.047 Adj. R2 = 0.045	N = 845 Social Portfolio Div. β = 0.214, b = 0.901, 95%CI[0.623, 1.179] p < .001 R2 = 0.046 Adj. R2 = 0.045	✅
Model 1 IV only IV – 0 for no interaction	N = 576 Social Portfolio Div. β = 0.241, b = 0.966, 95%CI[0.647, 1.285] p < .001 R2 = 0.058 Adj. R2 = 0.056	N = 962 Social Portfolio Div. β = 0.254, b = 1.098, 95%CI[0.833, 1.363] p < .001 R2 = 0.064 Adj. R2 = 0.063	✅

Model 2 results comparing original data and replication data

	Reanalyzed Original Results	Replication Results
Model 2 Control only Control – perc_time _social as in original paper	N = 577 perc_time_social β = 0.262, b = 1.528, 95%CI[1.068, 1.989] p < .001 R2 = 0.069 Adj. R2 = 0.067	N = 961 propSocialAsInOrigPaper β = 0.330, b = 1.946, 95%CI[1.593, 2.299] p < .001 R2 = 0.109 Adj. R2 = 0.108	✅
Model 2 Control only Control – Prop. episodes in-person	N = 578 Prop. ep. in-person β = 0.241, b = 1.493, 95%CI[1.000, 1.985] p < .001 R2 = 0.058 Adj. R2 = 0.056	N = 961 propInPersonEpisodes β = 0.320, b = 1.970, 95%CI[1.601, 2.339] p < .001 R2 = 0.103 Adj. R2 = 0.102	✅

References

Collins, H.K., Hagerty, S.F., Quiodbach, J., Norton, M.I., & Brooks, A.W. (2022). Relational diversity in social portfolios predicts well-being. Proceedings of the National Academy of Sciences, 119(43), e2120668119. https://doi.org/10.1073/pnas.2120668119 

Faul, F., Erdfelder, E., Buchner, A., & Lang, A.-G. (2009). Statistical power analyses using G*Power 3.1: Tests for correlation and regression analyses. Behavior Research Methods, 41, 1149-1160. Download PDF

Executive Summary

Transparency	Replicability	Clarity
	5 of 5 findings replicated

We ran replications of studies three (3) and four (4) from this paper. These studies found that:

• People have less support for behavioral nudges (such as sending reminders about appointment times) to prevent failures to appear in court than to address other kinds of missed appointments
• People view missing court as more likely to be intentional, and less likely to be due to forgetting, compared to other kinds of missed appointments
• The belief that skipping court is intentional drives people to support behavioral nudges less than if they believed it was unintentional

We successfully replicated the results of studies 3 and 4. Transparency was strong due to study materials and data being publicly available, but neither study being pre-registered was a weakness. Overall the studies were clear in their analysis choices and explanations, but clarity could have benefited from more discussion of alternative explanations and the potential for results to change over time.

Full Report

Study Diagrams

Study 3 Diagram

Study 4 Diagram

Replication Conducted

We ran a replication of studies 3 and 4 from: Fishbane, A., Ouss, A., & Shah, A. K. (2020). Behavioral nudges reduce failure to appear for court Science, 370(6517), eabb6591.
https://doi.org/10.1126/science.abb6591

How to cite this replication report: Transparent Replications by Clearer Thinking. (2023). Report #4: Replication of two studies from “Behavioral nudges reduce failure to appear for court” (Science | Fishbane et al. 2020). https://replications.clearerthinking.org/replication-2020Science370-6517
(Preprint DOI: https://doi.org/10.31234/osf.io/sb23t)

Key Links

• Go to the Research Box for this report to view our pre-registrations, experimental materials, de-identified data, and analysis files.
• See the predictions made about this study:
  • See the Manifold Markets prediction markets for this study:
    • For study 3 – 7.8% probability given to both claims replicating (corrected to exclude market subsidy percentage)
    • For study 4  – 21.4% probability given to all 3 claims replicating (corrected to exclude market subsidy percentage)
  • See the Metaculus prediction pages for this study
    • For study 3 – Community prediction was 49% “yes” for both claims replicating (note: some forecasters selected “yes” for more than one possible outcome)
    • For study 4 – Community prediction was 35% “yes” for all three claims replicating (note: some forecasters selected “yes” for more than one possible outcome)
• Download a PDF of the original paper
• View supporting materials for the original study on OSF

Overall Ratings

Our Replicability and Clarity Ratings are single-criterion ratings. Our Transparency Ratings are derived from averaging four sub-criteria (and you can see the breakdown of these in the second table).

Transparency: how transparent was the original study?
Replicability: to what extent were we able to replicate the findings of the original study?	All five findings from the original studies replicated (100%).
Clarity: how unlikely is it that the study will be misinterpreted?	Results were communicated clearly. Some alternative interpretations of the results could have been provided and the potential for the results to change over time could have been addressed.

Detailed Transparency Ratings

For an explanation of how the ratings work, see here.

Overall Transparency Rating:
1. Methods Transparency:	The materials were publicly available and almost complete, and remaining materials were provided on request.
2. Analysis Transparency:	The analyses for both studies 3 and 4 were commonly-completed analyses that were described in enough detail for us to be able to reproduce the same results on the original dataset.
3. Data availability:	The data were publicly available and complete.
4. Pre-registration:	Neither study 3 nor study 4 was pre-registered.

Summary of Study and Results

We replicated the results from laboratory experiments 3 and 4 from the original paper. The original paper conducted 5 laboratory experiments in addition to a field study, but we chose to focus on studies 3 and 4.

We judged study 3 to be directly relevant to the main conclusions of the paper and chose to focus on that first. Following communication with the original authorship team, who were concerned that study 3’s results may be affected by potential changes in public attitudes to the judicial system over time, we decided to expand our focus to include another study whose findings would be less impacted by changes in public attitudes (if those had occurred). We selected study 4 as it included an experimental manipulation. When considering one of the significant differences observed in study 4 between two of its experimental conditions (between the “mistake” and “control” conditions, explained below), we thought that this difference would only cease to be significant if the hypothetical changes in public opinion (since the time of the original study) had been very dramatic. 

Our replication study of study 3 (N = 394) and study 4 (N=657) examined: 

• Whether participants have lower support for using behavioral nudges to reduce failures to appear in court than for using behavioral nudges to reduce failures to complete other actions (study 3),  
• Whether participants rate failures to attend court as being less likely to be due to forgetting and more likely to be intentional, compared to failures to attend non-court appointments (study 3), and 
• The different proportions of participants selecting behavioral nudges three across different experimental conditions (study 4). 

The next sections provide a more detailed summary, methods, results, and interpretation for each study separately.

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Study 3 summary 

In the original study, participants were less likely to support using behavioral nudges (as opposed to harsher penalties) to reduce failures to appear in court than to reduce failures to attend other kinds of appointments. They also rated failures to attend court as being less likely to be due to forgetting and more likely to be intentional, compared to failures to attend non-court appointments. 

Study 3 methods

In the original study and in our replication, participants read five scenarios (presented in a randomized order) about people failing to take a required action: failing to appear for court, failing to pay an overdue bill, failing to show up for a doctor’s appointment, failing to turn in paperwork for an educational program, and failing to complete a vehicle emissions test.

For each scenario, participants rated the likelihood that the person missed their appointment because they did not pay enough attention to the scheduled date or because they simply forgot. Participants also rated how likely it was that the person deliberately and intentionally decided to skip their appointment.

Finally, participants were asked what they thought should be done to ensure that other people attend their appointments. They had to choose one of three options (shown in the following order in the original study, but shown in randomized order in our study): 

• (1) Increase the penalty for failing to show up
• (2) Send reminders to people about their appointments, or 
• (3) Make sure that appointment dates are easy to notice on any paperwork

The original study included 301 participants recruited from MTurk. Our replication included 394 participants (which meant we had 90% power to detect an effect size as low as 75% of the original effect size) recruited from MTurk via Positly.

Study 3 results

Hypothesis	Original result	Our result	Replicated?
Participants have lower support for using behavioral nudges to reduce failures to appear for court (described in a hypothetical scenario) than for using behavioral nudges to reduce failures to attend other kinds of appointments (described in four other scenarios).	+	+	✅
Participants rate failures to attend court as being:  (1) less likely to be due to forgetting and (2) more likely to be intentional, compared to failures to attend non-court appointments (captured in four different scenarios).	+	+	✅

In the original study, participants were less likely to support behavioral nudges to reduce failures to appear in court compared to failures to attend other appointments (depicted in four different scenarios) (M_court = 43%, SD = 50; M_{other actions} = 65%, SD = 34; paired t test, t(300) = 8.13, p < 0.001). Compared to failures to attend other kinds of appointments, participants rated failures to attend court as being less likely to be due to forgetting (M_court = 3.86, SD = 2.06; M_{other actions} = 4.24, SD = 1.45; paired t test, t(300) = 3.79, p < 0.001) and more likely to be intentional (M_court = 5.17, SD = 1.75; M_{other actions} = 4.82, SD = 1.29; paired t test, t(300) = 3.92, p < 0.001).

We found that these results replicated. There was a significantly lower level of support for behavioral nudges to reduce failures to appear for court (M_court = 42%, SD = 50) compared to using behavioral nudges to reduce failures to complete other actions (M_{other actions} = 72%, SD = 32; paired t test, t(393) = 12.776, p = 1.669E-31).

Participants rated failures to attend court as being less likely to be due to forgetting (M_court = 3.234, SD = 1.848) compared to failures to attend non-court appointments (M_{other actions} = 3.743, SD = 1.433); and this difference was statistically significant: t(393) = 7.057, p = 7.63E-12. 

Consistent with this, participants also rated failures to attend court as being more likely to be intentional (M_court = 4.972, SD = 1.804) compared to failures to attend non-court appointments conditions (M_{other actions} = 4.492, SD = 1.408); and this difference was statistically significant: t(393) = 6.295, p = 8.246E-10.

A table with these complete results is available in the appendices.

Interpreting the results of study 3

The authors make the case that people generally ascribe “greater intentionality to failures to appear.” They also argue that it is these beliefs that contribute to the stance that harsher penalties are more effective than behavioral nudges for reducing failures to appear.

We generally are inclined to believe that the results are representative of their interpretation. However, there was still room for the original authors to be clearer about the interpretation of their results, particularly with respect to the degree to which they thought their results might change over time. 

When our team first reached out to the original authors about replicating study 3 from their paper, they were concerned that the results may have changed over time due to documented changes in the public’s attitudes toward the judicial system since the time the studies were completed. On reflection, we agreed that it was an open question as to whether the results in study 3 would change over time due to changing public opinion towards the criminal justice system in response to major events like the murder of George Floyd. Unfortunately, however, the authors’ belief that the results were sensitive to (potentially changing) public opinions rather than representing more stable patterns of beliefs, was not mentioned in the original paper. 

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Study 4 summary

In the original study, participants read a scenario about failures to appear in court, then they were randomized into one of three groups – an “intentional” condition, where participants were asked to write one reason why someone would intentionally skip court, a “mistake condition,” where they were asked to write a reason someone would miss it unintentionally, and a “control” condition, which asked neither of those questions. All participants were then asked what should be done to reduce failures to appear. Participants in the “intentional” and “control” conditions chose to increase penalties with similar frequencies, while participants in the “mistake” condition were significantly more likely to instead support behavioral nudges (as opposed to imposing harsher penalties for failing to appear) compared to people in either of the other conditions. 

Study 4 methods

In the original study and in our replication, all participants read background information on summonses and failure-to-appear rates in New York City. This was followed by a short experiment (described below), and at the end, all participants selected which of the following they think should be done to reduce the failure-to-appear rate: (1) increase the penalty for failing to show up, (2) send reminders to people about their court dates, (3) or make sure that court dates are easy to notice on the summonses. (These were shown in the order listed in the original study, but we showed them in randomized order in our replication.)

Prior to being asked the main question of the study (the “policy choice” question), participants were randomly assigned to one of three conditions. 

• In the control condition, participants made their policy choice immediately after reading the background information. 
• In the intentional condition, after reading the background information, participants were asked to type out one reason why someone might purposely skip their court appearance, and then they made their policy choice. 
• In the mistake condition, participants were asked to type out one reason why someone might accidentally miss their court appearance, and then they made their policy choice.

The original study included 304 participants recruited from MTurk. Our replication included 657 participants (which meant we had 90% power to detect an effect size as low as 75% of the original effect size) recruited from MTurk via Positly.

Study 4 results

Hypotheses	Original results	Our results	Replicated?
(1) Participants are no less likely to support behavioral nudges in the “control” condition compared to in the “intentional” condition.	0	0	✅
(2) Participants are more likely to support behavioral nudges in the “mistake” condition than they are in the “control” condition.	+	+	✅
(3) Participants are more likely to support behavioral nudges in the “mistake” condition than they are in the “intentional” condition.	+	+	✅

In the original study, there was no statistically significant difference between the proportion of participants selecting behavioral nudges in the control versus the intentional condition (control: 63% supported nudges; intentional: 61% supported nudges; χ²(1, N = 304) = 0.09; p = 0.76). 

On the other hand, 82% of participants selected behavioral nudges in the mistake condition (which was a significantly larger proportion than both the control condition [χ²(1, N = 304) = 9.08; p = 0.003] and the intentional condition [χ²(1, N = 304) = 10.53; p = 0.001]).

In our replication, we assessed whether, similar to the original study, (1) participants in the “control” condition and the “intentional” condition do not significantly differ in their support for behavioral nudges; (2) Participants are more likely to support behavioral nudges in the “mistake” condition than they are in the “control” condition; and (3) Participants are more likely to support behavioral nudges in the “mistake” condition than they are in the “intentional” condition. We found that these results replicated:

(1)   χ² (1, N = 440) = 1.090, p = 0.296. Participants’ support for behavioral nudges in the control condition (where 64.3% selected behavioral nudges) was not statistically significantly different from their support for behavioral nudges in the intentional condition (where 69.0% selected behavioral nudges).

(2)   χ² (1, N = 441) = 34.001, p = 5.509E-9. Participants were more likely to support behavioral nudges in the mistake condition (where 88.0% selected behavioral nudges) than in the control condition (where 64.3% selected behavioral nudges).

(3)   χ² (1, N = 433) = 23.261, p = 1.414E-6. Participants were more likely to support behavioral nudges in the mistake condition (where 88.0% selected behavioral nudges) than in the intentional condition (where 69.0% selected behavioral nudges).

A table with these complete results is available in the appendices.

Interpreting the results of study 4

The original authors make the case that participants are more supportive of behavioral nudges instead of stiffer punishments when they think that people missed their appointments by mistake. The original authors noted that support for nudges to reduce failures to appear for court in Study 4 (in the control arm, 63% supported behavioral nudges) was higher than in Study 3 (where 43% supported behavioral nudges to reduce failures to appear for court). In the control arm of our replication of Study 4, we also found a higher support for nudges to reduce failures to appear (64% supported behavioral nudges) compared to in our replication of Study 3 (where 42% supported behavioral nudges to reduce failures to appear for court). The original authors attribute the difference to the background information (e.g., the baseline failure-to-appear rate) that was provided to participants in Study 4. Our results are consistent with their interpretation. 

We saw that participants assigned to the control and intentional conditions behaved similarly. The results seem to be consistent with the original study authors’ hypothesis that people default to thinking that failures to appear for court are intentional. In the original study, there had been a possible alternative interpretation: the control and intentional conditions could have both had similar responses because the top answer option on display was to increase penalties – in the original paper, the authors argued that the fact that participants in the control condition behaved similarly to the intentional condition was evidence for participants supporting penalties by default; but in their study, ordering effects would have been able to produce the same finding. In such a scenario, the mistake condition may have successfully pushed participants toward choosing one of the behavioral nudges, while neither the intentional condition nor control condition dissuaded people from selecting the first option they saw – i.e., the option that was displayed at the top of the list (to increase penalties). In contrast, in our replication, we shuffled the options in order to rule out order effects as an explanation for these results.

Although this was not mentioned in the original paper, certain biases may have contributed to some of the findings. One potential bias is demand bias, which is when participants change their behaviors or views because of presumed or real knowledge of the research agenda. With additional background information (compared to study 3), there may have been more of a tendency for participants to answer in a way that they believed that the researchers wanted them to. In the mistake condition, in particular, since participants were asked about how to reduce failures to appear immediately after being asked why someone would forget to attend, they may have guessed that the behavioral nudges were the responses that the experimenters wanted them to choose.  
The higher rate of behavioral nudge support in the mistake condition could also be at least partly attributable to social desirability bias. Social desirability bias occurs when respondents conceal their true opinion on a subject in order to make themselves look good to others (or to themselves). Participants in the mistake condition may have been reminded of the possibility of people not attending court due to forgetting, and may have selected a behavioral nudge in order to appear more compassionate or forgiving of forgetfulness (even if they did not support behavioral nudges in reality).

Conclusion

We gave studies 3 and 4 of this paper a 4/5 Transparency Rating (rounded up from 3.875 stars). The results from both studies replicated completely, supporting the original authors’ main conclusions. We think that there was room for the authors to be clearer about other interpretations of their data, including the possible influence of social desirability and demand bias, as well as their belief that their results may change over time. 

Acknowledgments

We would like to thank the original paper’s authorship team for their generous help in providing all necessary materials and providing insights prior to the replication. It was truly a pleasure to work with them. (However, the responsibility for the contents of the report remains with the author and the rest of the Transparent Replications team.)

I also want to especially thank Clare Harris for providing support during all parts of this process. Your support and guidance was integral in running a successful replication. You have been an excellent partner.  I want to thank Amanda Metskas for her strategic insights, guidance, and feedback to ensure I was always on the right path.  I want to finally thank Spencer Greenberg for giving me the opportunity to work with the team! 

Purpose of Transparent Replications by Clearer Thinking

Transparent Replications conducts replications and evaluates the transparency of randomly-selected, recently-published psychology papers in prestigious journals, with the overall aim of rewarding best practices and shifting incentives in social science toward more replicable research.

We welcome reader feedback on this report, and input on this project overall.

Appendices

Study 3 full table of results

Hypotheses	Original results	Our results
Participants have lower support for using behavioral nudges to reduce failures to appear for court (Mcourt) (described in a hypothetical scenario) than for using behavioral nudges to reduce failures to attend other kinds of appointments (Mother) (described in four other scenarios).	Mcourt = 43% SD = 50 Mother = 65% SD = 34 paired t-test t(300) = 8.13 p = 1.141E −14	Mcourt = 42% SD = 50 Mother = 72% SD = 32 paired t-test t(393) = 12.776 p = 1.669E-31	✅
Participants rate failures to attend court as being: (1) less likely to be due to forgetting and (2) more likely to be intentional, compared to failures to attend non-court appointments (captured in four different scenarios).	(1) Less likely forgetting: Mcourt = 3.86 SD = 2.06 Mother = 4.24 SD = 1.45 paired t-test t(300) = 3.79 p = 1.837E−4 (2) More likely intentional: Mcourt = 5.17 SD = 1.75; Mother = 4.82 SD = 1.29 paired t test, t(300) = 3.92 p = 1.083E−4	(1) Less likely forgetting: Mcourt = 3.23 SD = 1.85 Mother = 3.74 SD = 1.43 paired t-test t(393) = -7.057 p = 7.63E-12 (2) More likely intentional: Mcourt = 4.97 SD = 1.80 Mother = 4.49 SD = 1.41 paired t-test, t(393) = 6.30 p = 8.246E-10	✅

Study 4 full table of results

Hypotheses	Original results	Our results
(1) Participants are no less likely to support behavioral nudges in the “control” condition compared to in the “intentional” condition.	Control: 63% supported nudges Intentional: 61% supported nudges χ2(1, N = 304) = 0.09 p = 0.76	Control: 64% supported nudges Intentional: 69% supported nudges χ2 (1, N = 440) = 1.090 p = 0.296	✅
(2) Participants are more likely to support behavioral nudges in the “mistake” condition than they are in the “control” condition.	Control: 63% supported nudges Mistake: 82% supported nudges χ2(1, N = 304) = 9.08 p = 0.003	Control: 64% supported nudges Mistake: 88% supported nudges   χ2 (1, N = 441) = 34.001 p = 5.509E-9	✅
(3) Participants are more likely to support behavioral nudges in the “mistake” condition than they are in the “intentional” condition.	Intentional: 61% supported nudges Mistake: 82% supported nudges χ2(1, N = 304) = 10.53 p = 0.001	Intentional: 69% supported nudges Mistake: 88% supported nudges χ2 (1, N = 433) = 23.261 p = 1.414E-6	✅

At Transparent Replications we have introduced a study rating criterion that, to our knowledge, has not been used before. We call it our “clarity” rating, and it is an assessment of how unlikely it would be for a reader to misinterpret the results of the study based on the discussion in the paper. 

When a study replicates, it is natural to assume that the claims the paper makes based on that study are likely to be true. Unfortunately, this is not necessarily the case, as there may be a substantial gap between what a study actually demonstrated and what the paper claims was demonstrated. All a replication shows is that with new data you can get the same statistical result; it doesn’t show that the claims made based on the statistical result are correct. The clarity rating helps address this, by evaluating the size of the gap between what was shown and what was claimed.

It’s important that papers have a high level of “clarity.” When they don’t, readers may conclude that studies support conclusions that aren’t actually demonstrated by the tests that were conducted. This causes unproven claims to make their way into future research agendas, policymaking, and individual decision-making.

We acknowledge that making a paper clear is a difficult task, and we ourselves often have room for being clearer in our explanations of results. We also acknowledge that most authors strive to make their papers as clear and accurate as possible. A perfect “clarity” rating is very difficult to obtain, and when a paper loses points on this criterion, we are in no way assuming that the authors have intentionally introduced opportunities for misinterpretation – on the contrary, it seems to us that most potential misinterpretations are easier for an outside research team to see, and most original authorship teams would prefer to avoid misinterpretations of their results.  

We hope that evaluating clarity will also serve to detect and disincentivize Importance Hacking. Importance Hacking is a new term we’ve introduced to refer to when the importance, novelty, utility, or beauty of a result is exaggerated using subtle enough methods that it goes undetected by peer reviewers. This can (and probably often does) happen unintentionally. A variety of types of Importance Hacking exist, and they can co-occur. Each type involves exaggerating the importance of:

• Conclusions that were drawn: papers may make it seem like a study’s results support some interesting finding X when they really support something else (X′) which sounds similar to X but is much less interesting or important.
• Novelty: papers may discuss something in a way that makes it seem more novel or unintuitive than it is. Perhaps the result is already well-known or is something that almost everyone would already know based on common sense. 
• Usefulness: papers may overstate how useful a result will be for the world.
• Beauty: papers may make a result seem clean and beautiful when in fact, it’s messy or hard to interpret.

Given that there is limited attention, money, and time for scientific research, these Importance Hacked studies use up limited space, attention, and resources that could be directed to more valuable work.

While we believe that evaluating the clarity of papers is important, it does have the drawback that it is more subjective to evaluate than other criteria, such as replicability. We try to be as objective as possible by focusing first on whether a study’s results directly support the claims made in the paper about the meaning of those results. This approach brings into focus any gap between the results and the authors’ conclusions. We also consider the completeness of the discussion – if there were study results that would have meaningfully changed the interpretation of the findings, but that were left out of the paper’s discussion, that would lower the clarity rating.

When replicating studies, we aim to pre-register not only the original analyses, but also the simplest valid statistical test(s) that could address a paper’s research questions, even if these were not reported in the original paper. Sometimes more complex analyses obscure important information. In such cases, it is useful to report on the simple analyses so that we (and, importantly, our readers) can see the answer to the original research questions in the most straightforward way possible. If our redone analysis using the simplest valid method is consistent with the original result, that lends it further support.

We would encourage other projects aiming to evaluate the quality of papers to use our clarity criterion as well. Transparency and replicability are necessary, but not sufficient, for quality research. Even if a study has been conducted transparently and is replicable, this does not necessarily imply that the results are best interpreted in exactly the way that the original authors interpreted them.

To understand our entire ratings system, read more about our transparency and replicability ratings.

Transparent Replications rates the studies that we replicate on three main criteria: transparency, replicability, and clarity. You can read more about our transparency ratings here.

The replicability rating is our evaluation of the degree of consistency between the findings that we obtained in our replication study and the findings in the original study. Our goal with this rating is to give readers an at-a-glance understanding of how closely our results matched the results of the original study. We report this as the number of findings that replicated out of the total number of findings reported in the original study. We also convert this to a star rating (out of 5 stars). So if 50% of the findings replicated we would give the paper 2.5 stars, and if 100% of the findings replicated we would give 5 stars.

That initially sounds simple, but we had to make a few key decisions about what counts and what doesn’t when it comes to assessing whether findings replicate.

What findings count when replicating a study? 

Studies often examine several questions. Sometimes a table with many results will be presented, but only some of those results pertain to hypotheses that the researchers are testing. Should all of the presented results be considered when assessing how well a study replicates? If not, then how does one choose which results to consider?

Our answer to this question is that the results we consider to be the study’s findings are the ones that pertain to the primary hypotheses the researchers present in their paper. 

This means that if a table of results shows a significant relationship between certain variables, but that relationship isn’t part of the theory that the paper is testing, we don’t consider whether that result is significant in our replication study when assigning our replicability rating. For example, a study using a linear regression model may include socioeconomic status as a control variable, and in the original regression, socioeconomic status may have a significant relationship with the dependent variable. In the replication, maybe there isn’t a significant relationship between socioeconomic status and the dependent variable. If the original study doesn’t have any hypotheses proposing a relationship between socioeconomic status and their dependent variable, then that relationship not being present in the replication results would not impact the replicability rating of the study.

This also means that typically if a result is null in the original paper, whether it turns out to be null in the replication is only relevant to our ratings if the authors of the original paper hypothesized about the result being null for reasons driven by the claims they make in the paper.

We use this approach to determine which findings to evaluate because we want our replication to be fair to the original study, and we want our ratings to communicate clearly about what we found. If we included an evaluation of results that the authors are not making claims about in our rating, it would not be a fair assessment of how well the study replicated. And if a reader glances at the main claims of study and then glances at our replicability rating, the reader should get an accurate impression about whether our results were consistent with the authors’ main claims.

In our replication pre-registrations, we list which findings are included when evaluating replicability. In some cases this will involve judgment calls. For instance, if a statistic is somewhat but not very related to a key hypothesis in the paper, we have to decide if it is closely related enough to include. It’s important that we make this decision in advance of collecting data. This ensures that the findings that comprise the rating are determined before we know the replication results.

What counts as getting the same results?

When evaluating the replication results, we need to know in advance what statistical result would count as a finding replicating and what wouldn’t. Typically, for a result to be considered the same as in the original study, it must be in the same direction as the original result, and it must meet a standard for statistical significance.

There may be cases where the original study does not find support for one of the authors’ original hypotheses, but we find a significant result supporting the hypothesis in our replication study. Although this result is different from the results obtained in the original study, it is a result in support of the original authors’ hypothesis. We would discuss this result in our report, but it would not be included in the replicability rating because the original study’s null result is not considered one of the original study’s findings being tested in the replication (as explained above).

There have been many critiques of the way statistical significance is used to inform one’s understanding of results in the social sciences, and some researchers have started using alternative methods to assess whether a result should be considered evidence of a real effect rather than random chance. The way we determine statistical significance in our replication studies will typically be consistent with the method used in the original paper, since we are attempting to see if the results as presented in the original study can be reproduced on their own terms. If we have concerns about how the statistical significance of the results is established in the original study, those concerns will be addressed in our report, and may inform the study’s clarity rating. In such cases, we may also conduct extra analyses (in addition to those performed in the original paper) and compare them to the original paper’s results as well.

In some replication projects with very large sample sizes, such as Many Labs, a minimum effect size might also need to be established to determine whether a finding has replicated because the extremely high statistical power will mean that even tiny effects are statistically significant. In our case this isn’t likely to be necessary because, unless the original study was underpowered, the statistical power of our studies will not be dramatically larger than that of the original study.

In our replication pre-registrations, we define what statistical results we would count as replicating the original findings.

What does the replicability rating mean?

With this understanding of how the replicability rating is constructed, how should it be interpreted?

If a study has a high replicability rating, that means that conducting the same experiment and performing the same analyses on the newly collected data generated results that were largely consistent with the findings of the original paper.

If a study has a low replicability rating, it means that a large number of the results in the replication study were not consistent with the findings reported in the original study. This means that the level of confidence a person should have that the original hypotheses are correct should be reduced.

A low replicability rating for a study does not mean that the original researchers did something wrong. A study that is well-designed, properly conducted, and correctly analyzed will sometimes generate results that do not replicate. Even the best research has some chance of being a false positive. When that happens, researchers have the opportunity to incorporate the results from the replication into their understanding of the questions under study and to use those results to aid in their future investigations. It’s also possible that we will obtain a false negative result in a replication study (no study has 100% power to detect an effect).

The replicability rating also does not evaluate the validity of the original experiment as a test of the theory being presented, or whether the analyses chosen were the best analyses to test the hypotheses. Questions about the validity, generalizability, and appropriateness of the analyses are addressed in our “clarity” rating, not our “replicability” rating.

For these reasons, we encourage looking at the replicability rating in the context of the transparency and clarity ratings to get a more complete picture of the study being evaluated. For example, if a study with a high replicability rating received a low transparency rating, then the study didn’t use open science best practices, which means that we may not have had access to all the original materials needed to replicate the study accurately. Or in the case of a study with a high replicability rating, but a low clarity rating, we can infer that the experimental protocol generates consistent results, but that there may be questions about what those results should be understood to mean.

As we conduct more replications, we expect to learn from the process. Hence, our procedures (including those mentioned in this article) may change over time as we discover flaws in our process and improve it.

By rigorously evaluating studies using these three criteria (“transparency,” “replicability,” and “clarity”), we aim to encourage and reward the publication of reliable research results that people can be highly confident in applying or building on in future research. 

Transparent Replications is an initiative that celebrates and encourages openness, replicability, and clear communication in psychological science. We do this by regularly placing new papers from high-impact journals under the microscope. We select studies from them, run replications, and rate the replicated studies using three key criteria. Each of the three criteria represents a concept that we see as critical for good science,¹ and by rating papers based on these criteria, we hope that we will incentivize our target journals to value each concept more highly than they have done to date. In this series of posts, we explain the contents and rationale underlying each criterion. 

This post explains the first of our three criteria: transparency. This is a broad concept, so we have broken it down into subcriteria (explained below). We’ve designed the subcriteria with the aim to: 

1. Highlight and celebrate highly transparent studies, and
2. Encourage research teams who aren’t already maximally transparent to be more transparent in the future.

The sections below give a breakdown of our current criteria (as of January, 2023) for evaluating the transparency of studies. Of course, we are open to changing these criteria if doing so would enable us to better meet the goals listed above. If you believe we are missing anything, if you think we should be placing more emphasis on some criteria than on others, or if you have any other alterations you’d like to suggest, please don’t hesitate to get in touch!

Post Contents

• The components of transparency, why they’re important, and how we rate them:
  • Methods and Analysis Transparency
  • Data Transparency
  • Pre-registration
  • Open Access

• Are there circumstances in which it’s unfair to rate a study for its transparency?
• Transparency sheds light on our other criteria
• Summary
• Acknowledgements

The components of transparency, why they’re important, and how we rate them

Methods and Analysis Transparency

Research teams need to be transparent about their research methods and analyses so that future teams are able to replicate those studies and analyses. 

1. Our Methods Transparency Ratings (edited in May 2023²): 

• Did the description of the study methods and associated materials (potentially including OSF files or other publicly-accessible materials describing the administration of the study) give enough detail for people to be able to replicate the original study accurately?
  • 5 = The materials were publicly available and were complete.
  • 4.5 = The materials were publicly available and almost complete, and remaining materials were provided on request.
  • 4 = The materials were publicly available and almost complete; not all the remaining materials were provided on request, but this did not significantly impact our ability to replicate the study.
  • 3 = The materials were not publicly available, but the complete materials were provided on request (at no cost).
  • 2.5 = The materials were not publicly available, but some materials were provided on request. The remaining materials could be accessed by paying to access them.
  • 2 = The materials were not publicly available, but some materials were provided on request. Other materials were not accessible.
  • 1.5 = The materials were not publicly available, and were not provided on request. Some materials could be accessed by paying to access them.
  • 1 = We couldn’t access materials.

2. Our Analysis Transparency Ratings (edited in April 2023³): 

• Was the analysis code available?
  • 5 = The analysis code was publicly available and complete.
  • 4 = Either: (a) the analysis was a commonly-completed analysis that was described fully enough in the paper to be able to replicate without sharing code; OR (b) the analysis code was publicly available and almost complete – and the remaining details or remaining parts of the code were given on request.
  • 3.5 = The analysis code or analysis explanation was publicly available and almost complete, but the remaining details or remaining code were not given on request.
  • 3 = The analysis code or the explanation of the analysis was not publicly available (or a large proportion of it was missing), but the complete analysis code was given on request.
  • 2 = The analysis code was not publicly available or the explanation was not clear enough to allow for replication. An incomplete copy of the analysis code was given on request.
  • 1 = We couldn’t access the analysis code and the analysis was not explained adequately. No further materials were provided by the study team, despite being requested.

Data Transparency

Datasets need to be available so that other teams can verify that the findings are reproducible (i.e., so that others can verify that the same results are obtained when the original analyses are conducted on the original data). Publishing datasets also allows other teams the opportunity to derive further insights that the original team might not have discovered.

3. Our Data Availability Ratings (as of January 2023): 

• Were the data (including explanations of data) available?
  • 5 = The data were already publicly available and complete.
  • 4.5 = The data were publicly available and almost complete, and authors gave remaining data on request.
  • 4 = The data were publicly available and partially complete, but the remaining data were not given on request.
  • 3 = The data were not publicly available, but the complete dataset was given on request.
  • 2 = The data were not publicly available, and an incomplete dataset was given on request.
  • 1 = We couldn’t access the data.

Pre-registration

Pre-registration involves the production of a time-stamped document outlining how a study will be conducted and analyzed. A pre-registration document is written before the research is conducted and should make it possible for readers to evaluate which parts of the study and analyses eventually undertaken were planned in advance and which were not. This increases the transparency of the planning process behind the research and analyses. Distinguishing between pre-planned and exploratory analyses is especially helpful because exploratory analyses can (at least in theory) give rise to higher rates of type 1 errors (i.e., false positives) due to the possibility that some researchers will continue conducting exploratory analyses until they find a positive or noteworthy result (a form of p-hacking). Pre-registration can also disincentivize hypothesizing after the results are known (HARKing).

The fact that a team pre-registered a study is not sufficient grounds for that study to receive a high Pre-registration Rating when we evaluate a study’s transparency. For a perfect score, the pre-registration should be adhered to. If there are deviations from it, it is important that these are clearly acknowledged. If a study is pre-registered but the authors deviate from the pre-registration in significant ways and fail to acknowledge they have done so, this can give a false impression of rigor without actually increasing the robustness of the study. (We consider this a worse scenario than having no pre-registration at all, because it creates a false impression that the study and analyses were done in ways that aligned with previous plans.)

4. Our Pre-registration Ratings (as of January 2023): 

• Was the study pre-registered, and did the research team adhere to the pre-registration?
  • 5 = The study was pre-registered and the pre-registration was adhered to.
  • 4 = The study was pre-registered and was carried out with only minor deviations, all of which were acknowledged by the research team.
  • 3.5 = The study was pre-registered and was carried out with only minor deviations, but only some of these were acknowledged by the research team.
  • 3 = The study was pre-registered but was carried out with major deviations, all of which were acknowledged by the research team.
  • 2.5 = The study was pre-registered but was carried out with major deviations, only some of which were acknowledged, or there were significant parts of the experiment or analyses that were not mentioned in the preregistration.
  • 2 = The study was not pre-registered.
  • 1 = The study was pre-registered, but the pre-registration was not followed, and the fact that the preregistration wasn’t followed was not acknowledged by the authors.

Open Access

Another factor which we believe contributes to transparency, but which we do not currently consider when rating studies, is free availability. Papers that are not freely available tend to be accessible only by certain library users or paid subscribers. We do not rate studies based on their free availability because we do not think authors have enough power over this aspect of their papers. If you disagree with this, and think we should be rating studies on this, please get in touch.

Are there circumstances in which it’s unfair to rate a study for its transparency?

We acknowledge that there are some circumstances in which it would be inappropriate for a study to be transparent. Here are some of the main ones:

1. Information hazards might make it unsafe to share some research. If the dissemination of true information has the potential to cause harm to others, or to enable someone to cause harm, then the risk created through sharing that information is an information hazard, or infohazard. We expect that serious infohazards would arise relatively infrequently in psychological research studies. (Instead, they tend to arise in research disciplines more known for their dual-use research, such as biorisk research.) 
2. There may be privacy-related or ethical reasons for not sharing certain datasets. For example, certain datasets may only have been obtained on the condition that they would not be shared openly.
3. Certain studies may be exploratory in nature, which may make pre-registration less relevant. If a research team chose to conduct an exploratory study, they may not pre-register it. One could argue that exploratory studies should be followed up with pre-registered confirmatory studies prior to a finding being published. However, a team may wish to share their exploratory findings prior to conducting confirmatory follow-up studies.

If a study we evaluate has a good reason to not be fully transparent, we will take note of this and will consider not rating them on certain subcriteria. Of the reasons listed above, we expect that almost all the legitimate reasons for a lack of transparency will fall into the second and third categories. The first class of reasons – serious infohazards – are not expected to arise in the studies we replicate, because if we thought that a given psychology study was likely to harm others (either directly or through its results), we would not replicate it in the first place. On the other hand, the other two reasons seem relatively more likely to apply: we could end up replicating some studies that use datasets which cannot be shared, while other studies we replicate may be exploratory in nature and may not have been pre-registered. In such cases, depending on the details of the study, we may abstain from rating data transparency, or we may abstain from rating pre-registration (but only if the authors made it very clear in their paper that the study was exploratory in nature). 

Transparency sheds light on our other criteria

A study’s transparency tends to have a direct impact on our interpretation of its replicability ratings. The more transparent a study is, the more easily our team can replicate it faithfully (and the more likely it is that the findings will be consistent with the original study, all else being equal). Conversely, the less transparent the original study, the more likely it is that we end up having to conduct a conceptual replication instead of a direct replication. These two different types of replications have different interpretations.

Transparency also affects our Clarity Ratings. At Transparent Replications, when we talk about transparency, we are referring to the degree to which a team has publicly shared their study’s methods, analyses, data, and (through pre-registration) planning steps. There is another criterion which we initially discussed as a component of our Transparency Ratings (but which we eventually placed in its own separate criterion): whether the description and discussion of the results in the original paper match with what the results actually show. We consider it very important that teams describe and discuss their results accurately; they should also document their reasoning process transparently and soundly. However, we consider this aspect of transparency to be conceptually distinct enough that it belongs in a separate criterion: our Clarity criterion, which will be discussed in another post. To assess this kind of clarity, we first need the paper under examination to be transparent in its methods, analyses, and data. Consequently, a paper that has a high score in our Transparency Ratings is more likely to have an accurate rating in its Clarity criterion. 

Summary

Wherever possible, psychology studies should transparently share details of their planning process (through pre-registration), methods, analyses, and data. This allows other researchers, including our team, to assess the reproducibility and replicability of the original results, as well as the degree to which the original team’s conclusions are supported by their data. If a study receives a high rating on all our Transparency Ratings criteria, we can be more confident that our Replicability and Clarity Ratings are accurate. And if a study performs well on all three criteria, we can be more confident in the conclusions derived from it.

Acknowledgements

Many thanks to Travis Manuel, Spencer Greenberg, and Amanda Metskas for helpful comments and edits on earlier drafts of this piece.

Footnotes

1. We don’t think that our criteria (transparency, replicability, and clarity) are the only things that matter in psychological science. We also think that psychological science should be focusing on research questions that will have a robustly positive impact on the world. However, in this project, we are focusing on the quality of studies and their write-ups, rather than how likely it is that answering a given research question will improve the world. An example of a project that promotes similar values to those that our initiative focuses on, as well as promoting research with a large positive impact on the world is The Unjournal. (Note that we are not currently affiliated with them.)
2. We edited our Methods Transparency ratings following some discussions within our team from April to May, 2023. The previous Methods Transparency ratings had been divided into sub-criteria, labeled as (a) and (b). Sub-criterion (a) had rated the transparency of materials other than psychological scales , and sub-criterion (b) had rated the accessibility of any psychological scales used in a given study. Between April and May, 2023, we decided to merge these to sub-criteria into one criterion rating.
3. We added details to our Analysis Transparency ratings in April 2023, to cover cases where analysis code is not provided but the analysis method is simple enough to replicate faithfully without the code. For example, if the authors of a study present the results from a paired t-tests and if they provided enough information for us to be able to reproduce their results, the study would be given a four-star rating for Analysis Transparency, even if the authors did not provide any details as to which programming language or software they used to perform the t-tests.

Sigal Samuel’s article, “Lots of bad science still gets published. Here’s how we can change that.” in Vox today, highlights the work we’re doing at Transparent Replications to address the replication crisis in psychology research.

If you’ve found your way here from the article, welcome! Check out our first three published replications from Nature, JPSP volume 122 issue 2, and JPSP volume 122 issue 3.

If you’d like us to let you know when we publish replication reports, subscribe to our email list. We promise that we’ll only message a few times per month.

We would also love to get your feedback on our work.

Listen to project founder, Spencer Greenberg, discuss Transparent Replications on the Two Psychologists Four Beers podcast.

If you’ve found your way here from the podcast episode, welcome! Check out our first three published replications from Nature, JPSP volume 122 issue 2, and JPSP volume 122 issue 3.

If you’d like us to let you know when we publish replication reports, subscribe to our email list. We promise we only message a few times per month.

We would also love to get your feedback on our work.

Executive Summary

Transparency	Replicability	Clarity

We ran a replication of study 2A from this paper, which tested whether knowing additional information about another person changed what participants thought the other person would know about them. The primary result in the original study failed to replicate. There was no relationship between whether participants were given information about their ‘partner’ and how likely the participants thought their ‘partner’ would be to detect a lie the participant told.

Full Report

Study Diagram

Replication Conducted

We ran a replication of Study 2A from: Shah, A.K., & LaForest, M. (2022). Knowledge about others reduces one’s own sense of anonymity. Nature, 603, 297–301. https://doi.org/10.1038/s41586-022-04452-3

How to cite this replication report: Transparent Replications by Clearer Thinking. (2022). Report #3: Replication of a study from “Knowledge about others reduces one’s own sense of anonymity” (Nature | Shah & LaForest 2022) https://replications.clearerthinking.org/replication-2022nature603
(Preprint DOI: https://doi.org/10.31234/osf.io/xjaty)

Key Links

• The data collected in the replication study is available for download as a .csv file.
• The experimental materials can be previewed on GuidedTrack.
• The experiment code is available to view or copy on GuidedTrack (free login required).
• Download a PDF of the JASP Output
  • Primary Analyses – N = 475 Entire Sample
  • Secondary Analyses – N = 270 Manipulation Check Passed Subsample
  • Additional Analyses – N = 430 Comprehension Check Passed Subsample
  • Additional Analyses – N = 244 Man. & Comp. Checks Both Passed Subsample
• Our Preregistration is available at AsPredicted.
• Manifold Markets predicted a 62% probability of this study replicating.
• Metaculus predicted a 69% probability of this study replicating.
• Download a PDF of Shah & LaForest’s original paper.
• The supporting materials for the original paper can be found on OSF.

Overall Ratings

To what degree was the original study transparent, replicable, and clear?

Transparency:  how transparent was the original study?	Between information provided on OSF and responsive communication from the authors, it was easy to conduct a replication of this study; however, the authors did not pre-register the 9 laboratory experiments in this paper.
Replicability: to what extent were we able to replicate the findings of the original study?	The main finding did not replicate. Participants having information about another person did not increase belief by the participants that the other person could detect their lie in either the entire sample or an analysis on only those who passed the manipulation check. The finding that participants said they knew another person better if they were given information about them replicated in both the entire sample and the sample of those who passed the manipulation check, indicating that the manipulation did have some impact on participants. The replication of the mediation analysis is a more complicated question given that the main finding did not replicate.
Clarity: how unlikely is it that the study will be misinterpreted?	The explanation of this study in the paper is clear, and the statistics used for the main analysis are straightforward and easy to interpret.

Detailed Transparency Ratings

Overall Transparency Rating:
1. Methods Transparency:	The code used to program the study materials was provided on OSF. Authors were responsive to any remaining questions after reviewing the provided code.
2. Analysis Transparency:	Analysis code was not available because the analysis was conducted using SPSS. Authors were responsive to questions. Analyses were described clearly, and the analyses used were not needlessly complex or esoteric. The results reported in the paper could be reproduced easily using the data provided online by the authors.
3. Data availability:	Data were available on OSF.
4. Pre-registration:	No pre-registration was submitted for Study 2A or the other 8 lab studies conducted between 2015-2021 in the paper. The field study was pre-registered.

Summary of Study and Results

Study Summary

Our replication study (N = 475) examined whether people assigned a higher probability to the chance of another person detecting their lie if they were given information about that other person than if they were not. We found that the main result from the original study did not hold in our replication.

In the experiment, participants wrote 5 statements about themselves, 4 truths and 1 lie, and were told those statements would be shared with another person who would guess which one was the lie. Participants were either given 4 true statements about their ‘partner’ (information condition), or they were given no information about their ‘partner’ (no information condition). Participants were asked to assign a percentage chance to how likely their ‘partner’ would be to detect their lie after either being given this information or not. Note that participants in the study were not actually connected to another person, so for clarity we put the term ‘partner’ in single quotes in this report. 

We collected data from 481 participants using the Positly platform. We excluded 4 participants who were missing demographic data. We also excluded 2 participants who submitted nonsensical single word answers to the four truths and a lie prompt. Participants could not proceed in the experiment if they left any of those statements blank, but there was no automated check on the content of what was submitted. The authors of the original study did not remove any subjects from their analysis, but they recommended that we do this quality check in our replication.

The data were analyzed primarily using two-tailed independent samples t-tests. The main analysis asked whether participants in the information condition assigned a different probability to the chance of their ‘partner’ detecting their lie than participants in the no information condition. We found that this main result did not replicate (M_info = 33.19% (30.49–35.89%), n = 236 / M_{no info} = 33.00% (30.15–35.85%), n = 239; Welch’s t: ​​t(472.00) = 0.095; p = 0.924; Effect size: d = 0.009).

Detailed Results

Primary Analyses

Table 1: Results – Entire Sample

Hypothesis	Original Study Result	Our Replication Result	Result Replicated?
H1: Participants in the information condition will report a significantly higher percentage chance of lie detection by their ‘partner’ than participants in the no information condition.(entire sample)	Minfo = 41.06% (37.76–44.35%) n = 228;  Mno info = 33.29% (30.34–36.24%) n = 234  Welch’s t: ​​ t(453.20) = 3.44  p <0.001 Effect size: d = 0.32	Minfo = 33.19% (30.49–35.89%) n = 236 Mno info = 33.00% (30.15–35.85%) n = 239 Welch’s t: ​​t(472.00) = 0.095 p = 0.924 Effect size: d = 0.009	No
H2: Participants in the information condition will report significantly higher responses to how well they believe they know their ‘partner’. (entire sample)	Minfo = 3.04 95% CI = 2.83–3.25 n = 228;  Mno info = 1.89 95% CI = 1.69–2.09 n = 234  Student’s t: t(460) = 7.73,  p <0.001 Effect size: d = 0.72	Minfo = 2.65 95% CI = 2.47–2.84, n = 236 Mno info = 1.61 95% CI = 1.45–1.77 n = 239 Student’s t: t( 473.00 ) = 8.387 Welch’s t: ​​ t(464.53) = 8.381 p < 0.001 for both Effect size: d = 0.770 (Student’s), d = 0.769 (Welch’s)	Yes
H3: Knowledge of the ‘partner’ mediates the relationship between the condition participants were assigned to and their assessment of the percentage chance that their ‘partner’ will detect their lie. (entire sample)	indirect effect = 3.83 bias-corrected 95% CI = 1.91–5.99	indirect effect = 2.83 bias-corrected 95% CI = 1.24–4.89	See Discussion

Contingency Test

In the original study, the authors found that participants in the information condition were more likely to believe that they were connected to another person during the experiment than participants in the no information condition. Original study results: (58.3% (information condition) versus 40.6% (no information condition), χ2 = 14.53, p < 0.001, Cramer’s V = 0.18). Due to this issue, they ran their analyses again on only those participants who passed the manipulation check.

We performed the same contingency test as part of our replication study, and we did not have the same issue with our sample. Replication study results: (59.3% (information condition) versus 54.4% (no information condition), χ2 = 1.176, p = 0.278, Cramer’s V = 0.05). Despite not having this difference in our sample, we ran the same three tests on the subjects who passed the manipulation check (n = 270), as they did in the original study. These results are consistent with the results we obtained on our entire sample.

Secondary Analyses

Table 2: Results – Manipulation Check Passed Subsample

Hypothesis	Original Study Result	Our Replication Result	Result Replicated?
H4: Participants in the information condition will report a significantly higher percentage chance of lie detection by their ‘partner’ than participants in the no information condition.(manipulation check passed only)	Minfo = 44.69% (40.29-49.09%), n = 133 Mno info = 35.60% (30.73-40.47%), n = 95  Student’s t: ​​ t(226) = 2.69 p =0.008 Effect size: d = 0.36	Minfo = 33.91% (30.41–37.42%), n = 140 Mno info = 34.09% (30.11–38.05%), n = 130 Student’s t: t(268) = -0.64 Welch’s t: ​​ t(261.24) = -0.063  p = 0.95 for each test Effect size: d = -0.008 for both	No
H5: Participants in the information condition will report significantly higher responses to how well they believe they know their ‘partner’. (manipulation check passed only)	Minfo = 3.44, 95% CI = [3.15, 3.73] n = 133 Mno info = 2.53, 95% CI = [2.14, 2.92] n = 95  Welch’s t: ​​t(185.48) = 3.67 p < 0.001 Effect size: d = 0.50	Minfo = 2.93, 95% CI = [2.68, 3.18] n = 140 Mno info = 1.89, 95% CI = [1.62, 2.15] n = 130 Welch’s t: ​​ t(266.05) = 5.66  p < 0.001 Effect size: d = 0.689	Yes
H6: Knowledge of the ‘partner’ mediates the relationship between the condition participants were assigned to and their assessment of the percentage chance that their ‘partner’ will detect their lie. (manipulation check passed only)	indirect effect = 4.18 bias-corrected 95% CI = [1.64, 7.35]	indirect effect = 3.25 bias-corrected 95% CI = [1.25, 5.8]	See Discussion

Additional Analyses

We had a concern that participants who were not carefully reading the experimental materials may not have understood which information of theirs was being shared with their ‘partner’ in the study. To address that concern, we reminded participants that their ‘partner’ would not be told which of the 5 statements they shared was a lie. We also added a comprehension check question at the end of the experiment after all of the questions from the original experiment were asked. We found that 45 of 475 participants (9%) failed the comprehension check, which was a 4 option multiple choice question. Re-running the analyses excluding those who failed the comprehension check did not substantively change any of the results. (See Appendix for the specific language used in the reminder, and for the full table of these results.)

Interpreting the Results

Is Mediation Analysis appropriate without a significant total effect?

There is debate about whether it is appropriate to conduct a mediation analysis when there is no significant total effect. Early approaches to mediation analysis used a causal steps approach in which the first step was testing for the relationship between X and Y, and then testing for mediation if there is a significant X-Y relationship. In that approach a test for mediation is only done if a significant relationship exists for the total effects (Baron & Kenney, 1986). More recently, approaches to mediation analysis have been developed that do not rely on this approach, and the developers of more modern mediation analysis methods have argued that it can be appropriate to run a mediation analysis even when there is no significant X-Y relationship (Rucker et al, 2011; Hayes, 2013). 

Some recent research attempts to outline the conditions under which it is appropriate to conduct a mediation analysis in the absence of a significant total effect (Agler & De Boeck, 2017; Loeys, Moerkerke & Vansteelandt, 2015). The conditions under which this is an appropriate step to take are when there is an a priori hypothesis that the mediated relationship is the important path to examine. That hypothesis could account for one of two situations in which an indirect effect might exist when there is no significant total effect:

1. The direct effect and the indirect effect are hypothesized to have opposite signs. In this case, the total effect could be non-significant because the direct and the indirect effects cancel.
2. There is hypothesized complete mediation (all of the effect in the total effects model is coming from the indirect rather than the direct path), and the statistical power of the total effects model is low. In this case the indirect effects model can offer more statistical power, which can lead to finding the indirect relationship that exists, despite the Type II error leading to incorrectly failing to reject the null-hypothesis in the total effects model.

Agler & De Boeck, 2017 and Loeys, Moerkerke & Vansteelandt, 2015 recommend against conducting a mediation analysis when there is no significant total effects model result unless there is a prior hypothesis that justifies that analysis. This is the case for the following reasons:

1. Mediation analysis without a significant total effect greatly increases the chances for a Type I error on the indirect path, inflating the chances of finding a statistically significant indirect effect, when no real indirect effect exists.
2. Mediation analysis can result in false positives on the indirect path that are caused by uncontrolled additional variables that influence both the mediator variable and the outcome variable. In a controlled experiment where the predictor variable is the randomized control, a total effects model of X → Y is not subject to the problem of uncontrolled additional variables, but once the mediator is introduced that problem re-emerges on the M → Y path.

Figure 1 from Loeys, Moerkerke & Vansteelandt, 2015 illustrates this issue.

It is difficult to tell from the original study if the mediation analysis was hypothesized a priori because no pre-registration was filed for the study. The way the results are presented in the paper, the strongly significant relationship the authors find between the experimental condition and the main dependent variable, the prediction of lie detection, is given as the main finding (it is what is presented in the main table of results). The mediation analysis is described in the text as something done subsequently that supports the theorized mechanism connecting the experimental condition and the main dependent variable. There is no reason to expect from the paper that the authors believe that there would be a canceling effect between the direct and indirect effects, in fact that would be contrary to their hypothesized mechanism. And with 462 participants, their study doesn’t seem likely to be underpowered, although they did not conduct a power analysis in advance.

How should the Mediation Analysis results be understood?

We carried out the mediation analysis, despite the debate in the literature over its appropriateness in this circumstance, because we did not specify in the pre-registration that we would only conduct this analysis if the total effect was significant.

The mediation analysis (see tables 1 and 2 above) does show a significant result for the indirect path: 

condition → knowThem → percentLieDetect

Digging into this result a bit more, we can identify a possible uncontrolled additional variable influencing both the mediator variable and the outcome variable that could account for the significant result on path b knowThem → percentLieDetect. First, here is the correlation between knowThem and percentLieDetect for the sample as a whole:

The troubling pattern we find is that random assignment to one condition or the other results in a distinct difference in whether participants’ responses to how well they know their ‘partner’ correlates with their assessment of how likely their ‘partner’ is to detect their lie.  In the no information condition, there is a significant correlation between how well participants say they know their ‘partner’ and how high a percentage they assign to their ‘partner’ detecting their lie. 

This relationship does not exist in the information condition. This means that, if a participant is given information about their ‘partner’, there is no relationship between how well they say they know their ‘partner’ and the percent chance they assign to their ‘partner’ detecting their lie.

Examining the scatter plot of the relationship between the two variables in the two conditions as well as the distribution of each variable in both conditions can help shed some light on why this might be.

Why might this relationship exist in the no information condition, but not the information condition? One possible explanation is that the participants in the no information condition have a large cluster of responses at one point – an answer of ‘1’ on the knowThem question, and an answer of 20% on the percentLieDetect question. In our sample just over 25% of respondents in the no information condition gave this pair of responses. That response is the floor value on the knowThem question, and it’s at the low end on the percent question, where responses could range from 0-100. 

It is not surprising that a large number of respondents in a condition where they have no information about their ‘partner’ would answer that they don’t know their partner at all, an answer of 1 on the 1-7 scale for the knowThem question. It is also understandable that a large portion of these respondents would also give an answer of 20% on the question of how likely they think their ‘partner’ would be to detect their lie, because that answer is the random chance that the one lie would be selected from five total statements. This pattern of responding suggests a group of participants in the no information condition who correctly understand that they don’t know anything about their ‘partner’ and their ‘partner’ doesn’t know anything about them.

Because the point that these 25% of respondents’ answers clustered at was near the floor on both variables, a statistically significant correlation is likely to occur even if the rest of the responses are random noise. We conducted a simulation which demonstrates this. 

We constructed simulated data the size of the sample of our no information condition (N = 239). The simulated data contained a fraction of responses at 1 for knowThem and 20% for percentLieDetect (the signal fraction), and the remaining fraction was assigned randomly to values from 1-7 for knowThem and 0-100% for percentLieDetect (the noise fraction). We then looked at the correlation coefficient for the simulated data. We ran this simulation 10,000 times at each of 3 different noise fractions. The graph shows the probability density of a correlation coefficient being generated by the simulations.

In yellow, there are 25% of respondents in the signal fraction at 1 and 20%, and 75% noise. That is similar to the percent of respondents who answered 1 and 20% in the no information group in the replication. When the pattern of 75% noise responses and 25% at 1 and 20% responses is simulated 10,000 times, typically it results in a correlation between 0.25 and 0.3. The correlation in our actual data is 0.26. 

Note that as the percentage of respondents anchored at the one point increases, from 10% in the green to 25% in the yellow to 90% in the blue, the strength of the correlation increases, as long as there are at least some random noise responses to create other points for the correlation line to be drawn through.

The python code used to run this simulation and generate this graph is available in the appendix.

This result suggests that the significant result in the indirect path of the mediation analysis in our replication could be the result of a statistical artifact in the no information condition in the relationship between the mediator variable knowThem and the dependent variable percentLieDetect. In the absence of a significant total effects relationship between the experimental condition and the main dependent variable, and given this potential cause of the knowThem→percentLieDetect relationship on the indirect path, the significant effect in the indirect path in the mediation analysis cannot be considered strong evidence. 

Conclusion

The big question that this pattern of results drives us to ask is ‘Why did the authors get such a strongly significant result in their sample, if there is really no relationship between the experimental condition and their main DV?’ Since we were surprised to go from a result in the initial paper with significance of p < 0.001 to a significance level of p > 0.90 in the replication we did several checks to help make sure that there were no coding errors in our data or other explanations for our results. 

One possible explanation for the large difference between the replication results and the results in the initial study could be the confounding of the success of the manipulation check with the experimental condition reported in the original study. In the original study data fewer people in the no information condition (only 40%) believed that they had been connected to another person in the study, while 58% of the participants in the information condition believed that they were connected to another participant in the study. The authors reported finding this in their contingency test. The attempt that the authors made to resolve this problem by running their analyses again on only those who passed the manipulation check may have created a selection bias since the people who passed the manipulation check and the people who failed it were not necessarily random. It is also possible that other sample differences could account for this difference in results.

A potential lesson from the failure of this study to replicate is that sample oddities, like the confounding between the success of the manipulation and the experimental condition in this paper, may have deeper implications for the results than are easily recognized. In this case, much to the authors’ credit, the authors did the contingency test that revealed this oddity in their sample data, they reported the potential issue posed by this result, and they conducted a subsequent analysis to attempt to address this issue. What they did seemed like a very reasonable solution to the oddity in their sample, but upon replication we learned that it may not be an adequate solution.

Author Acknowledgement

We are grateful to Dr. Anuj K. Shah and Dr. Michael LaForest for the feedback provided on the design and execution of this replication. Any errors or issues that may remain in this replication effort are the responsibility of the Transparent Replications by Clearer Thinking team.

We provided a draft copy of this report to the authors for review on October 17, 2022. 

We appreciate Dr. Shah and Dr. LaForest for their commitment to replicability in science, and for their transparency about their methods that made this replication effort possible.

Thank you to Spencer Greenberg and Clare Harris at Transparent Replications who provided valuable feedback on this replication and report throughout the process. Thank you also to Eric Huff for assistance with the simulation, and Greg Lopez for reviewing the report and analyses. Finally, thanks to the Ethics Evaluator for their review, and to the participants for their time and attention.

Purpose of Transparent Replications by Clearer Thinking

Transparent Replications conducts replications and evaluates the transparency of randomly-selected, recently-published psychology papers in prestigious journals, with the overall aim of rewarding best practices and shifting incentives in social science toward more replicable research.

We welcome reader feedback on this report, and input on this project overall.

Appendices

Additional Information about the Study

The wording in our replication study was the same as that of the original study, with the exception that we added a clarifying reminder to participants that their ‘partner’ would not be told which of their 5 statements was a lie. In the course of suggesting revisions to our replication study materials, the original author team reviewed the reminder language and did not express any concerns about it.

In the information condition, the original study wording was, “We have connected you to another person on the server and showed them your five statements.” Our wording in the information condition was, “We have connected you to another person on the server. We showed them all five of your statements and we did NOT tell them which ones were true.” For both the original study and our study, participants in the information condition then saw four true statements about their ‘partner.’ The statements used were the same in the original study and our replication.

In the no information condition, the original study wording was, “We have connected you to another person on the server and showed them your five statements.” Our wording in the no information condition was, “We have connected you to another person on the server. While we didn’t show you any information about the other person, we showed them all five of your statements and we did NOT tell them which ones were true.”

Additional Analyses

Detailed Results excluding participants who failed a comprehension check

Table 3: Results – Replication Sample with Exclusions

Hypothesis	Entire Replication Sample Excluding Failed Comprehension Check	Manipulation Check Passed Replication Subsample Excluding Failed Comprehension Check	Result Replicated?
Participants in the information condition will report a significantly higher percentage chance of lie detection by their ‘partner’ than participants in the no information condition.	Minfo = 32.81% (30.03–35.58%), n = 211;  Mno info = 32.44% (29.46–35.42%), n = 219  Welch’s t: ​​ t(426.80) = 0.175  p = 0.861 Effect size: d = 0.017	Minfo = 33.58% (29.98–37.17%), n = 125 Mno info = 33.73% (29.60–37.86), n = 119 Welch’s t: ​​t(235.78) = -0.056 p = 0.956 Effect size: d = -0.007	No
Participants in the information condition will report significantly higher responses to how well they believe they know their ‘partner’.	Minfo = 2.60, 95% CI = [2.41, 2.79] n = 211;  Mno info = 1.54, 95% CI = [1.39, 1.70] n = 219  Student’s t: t(428) = 8.54 Welch’s t: ​​t(406.93) = 8.51 p < 0.001 for both Effect size: d = 0.824 (Student’s) 0.822 (Welch’s)	Minfo = 2.81, 95% CI = [2.54, 3.07] n = 125 Mno info = 1.77, 95% CI = [1.52, 2.02] n = 119 Student’s t: t(242) = 5.55 Welch’s t: ​​t(241.85) = 5.56 p < 0.001 for both Effect size: d = 0.711 (Student’s), d = 0.712 (Welch’s)	Yes
Knowledge of the ‘partner’ mediates the relationship between the condition participants were assigned to and their assessment of the percentage chance that their ‘partner’ will detect their lie.	indirect effect = 2.39 bias-corrected 95% CI = 0.50–4.66	indirect effect = 2.92 bias-corrected 95% CI = 0.84–6.00	See Discussion

Analysis Code

Python Code for Simulation

References

Agler, R. and De Boeck, P. (2017). On the Interpretation and Use of Mediation: Multiple Perspectives on Mediation Analysis. Frontiers in Psychology 8: 1984. https://doi.org/10.3389/fpsyg.2017.01984 

Baron, R. M., & Kenny, D. A. (1986). The moderator–mediator variable distinction in social psychological research: Conceptual, strategic, and statistical considerations. Journal of Personality and Social Psychology, 51(6), 1173–1182. https://doi.org/10.1037/0022-3514.51.6.1173

Hayes, A. F. (2013). Introduction to mediation, moderation, and conditional process analysis: A regression-based approach. Guilford Press.

Loeys, T., Moerkerke, B. and Vansteelandt, S. (2015). A cautionary note on the power of the test for the indirect effect in mediation analysis. Frontiers in Psychology 5: 1549. https://doi.org/10.3389/fpsyg.2014.01549 

Rucker, D.D., Preacher, K.J., Tormala, Z.L. and Petty, R.E. (2011). Mediation Analysis in Social Psychology: Current Practices and New Recommendations. Social and Personality Psychology Compass, 5: 359-371. https://doi.org/10.1111/j.1751-9004.2011.00355.x

Shah, A.K., & LaForest, M. (2022). Knowledge about others reduces one’s own sense of anonymity. Nature, 603, 297–301. https://doi.org/10.1038/s41586-022-04452-3

Executive Summary

Transparency	Replicability	Clarity
	13 of 17 findings replicated

We ran a replication of study 3 from this paper, which assessed men’s and women’s beliefs about hypothetical scenarios in which they imagined applying to and working for technology companies with different ratios of men and women on staff (either 3:1 or 1:1). In the original study, when a company had a male:female staff ratio of 3:1 (even if its promotional materials display an equal balance of men and women), it was perceived as not being sincerely interested in increasing gender diversity, and women (but not men) were more likely to have identity threat concerns about working there (e.g., concerns about not having their contributions valued due to their gender). Also, both men and women (but especially women) tended to be less interested in working for that organization. These effects were mediated by the perception that the company was not sincerely interested in increasing gender diversity. Our findings were mostly consistent with those of the original study (see full report), except that we did not find that gender moderated the indirect effects of company diversity on interest in working for the company.

Full Report

Study Diagram

Replication Conducted

We ran a replication of Study 3 from: Kroeper, K. M., Williams, H. E., & Murphy, M. C. (2022). Counterfeit diversity: How strategically misrepresenting gender diversity dampens organizations’ perceived sincerity and elevates women’s identity threat concerns. Journal of Personality and Social Psychology, 122(3), 399-426. https://doi.org/10.1037/pspi0000348

How to cite this replication report: Transparent Replications by Clearer Thinking. (2022). Report #2: Replication of a study from “Counterfeit Diversity: How Strategically Misrepresenting Gender Diversity Dampens Organizations’ Perceived Sincerity and Elevates Women’s Identity Threat Concerns” (JPSP | Kroeper, Williams & Murphy 2022).
https://replications.clearerthinking.org/replication-2022jpsp122-3
(Preprint DOI: https://doi.org/10.31234/osf.io/uy2xt)

Key links

• Read our pre-registration 
• Download a .csv of our de-identified data
• View or copy our GuidedTrack code for the experiment (free login required to access)
• Preview the experiment
• Download our analysis scripts and files:
  • The PROCESS script used (downloaded from Andrew Hayes’ site)
  • Conditional process analysis script (you must run the script above before running this one)
  • Manipulation check
  • Descriptive statistics – all participants
  • Descriptive statistics – female participants
  • Descriptive statistics – male participants
  • Descriptive statistics on diversityExpectation variable of original dataset (long)
• See the (inaccurate) predictions made about this study:
  • See the Manifold Markets prediction market for this study – in that market, the community assigned an equal probability to 5, 6, 7, 8, 9, 10, 11, 12, or 13 findings replicating (of the 17 findings being considered), and they assigned each of those values 13.3 times higher probabilities than values outside that range. This works out to about a 10.3% chance of exactly 13 findings replicating according to Manifold.
  • See the Metaculus prediction page for this study – Metaculus predicted that 7.5 of the 17 findings would replicate. According to Metaculus, there was about a 3% chance of 13 findings (12.5-13.5 findings) replicating.
• Download a PDF of the original paper
• View supporting materials for the original study on OSF

Overall Ratings

To what degree was the original study transparent, replicable, and clear?

Transparency: how transparent was the original study?	Apart from aspects of the pre-registration process, this study had almost perfect ratings on all Transparency Ratings criteria.
Replicability: to what extent were we able to replicate the findings of the original study?	17 statistically significant findings were identified as most relevant (to the key hypotheses) among the findings recorded in the two results figures in the original study. 13 of those 17 findings replicated (76.5%).
Clarity: how unlikely is it that the study will be misinterpreted?	The (i) methods &/or (ii) results could be misinterpreted if readers don’t read (i) the textbook about methods, &/or (ii) supplementary materials.

Detailed Transparency Ratings

Overall Transparency Rating:
1. Methods Transparency:	Publicly-accessible materials described the administration of the study in enough detail for us to be able to replicate the original study accurately. The scales used were publicly available and were easy to find within the OSF materials.
2. Analysis Transparency:	The authors were very transparent about the analysis methods they used and readily communicated with us about them in response to our questions. Please see Appendices for details.
3. Data availability:	All data were publicly available and were easy to find on the OSF project site.
4. Pre-registration:	The authors pre-registered the study, but there were some deviations from this pre-registration, as well as a set of analyses (that formed the main focus of the discussion and conclusions for this study) that were not mentioned in the pre-registration. Please see Appendices for details.

Summary of Study and Results

• The study assessed men’s and women’s beliefs about working for technology companies with different ratios of men and women (either 3:1 or 1:1) among their staff. Participants reacted to a hypothetical scenario in which they considered applying for, obtaining, then commencing a project management position in the tech industry.  
• For an explanation of the statistical terms and analysis used in this write-up, please see the Explanations of statistical terms in the Appendix.
• The study’s findings were as follows. When a tech company had a male:female staff ratio of 3:1 (even if its promotional materials displayed an equal balance of men and women), it was perceived as not being sincerely interested in increasing gender diversity, and women (but not men) were more likely to have identity threat concerns about working there (e.g., concerns about being left out or stereotyped, or not having their contributions valued due to their gender). Also, both men and women (but especially women) tended to be less interested in working for that organization. These effects were mediated by the perception that the company was not sincerely interested in increasing gender diversity, and these indirect effects were moderated by participant gender.
• Our findings were mostly consistent with those of the original study (see details below), except that we did not find that gender moderated the indirect effects of company diversity on interest in working for the company via the perception of the company’s sincere interest in increasing gender diversity. Instead, we found that there were similarly significant indirect effects of company diversity on interest to work for the company, via the perception of the company’s sincere interest in increasing gender diversity, for both men and women. In their original paper, the authorship team had highlighted how experiments 1 and 2 had not shown this moderation relationship, while experiments 3 and 4 had.

Study Summary

This study assessed men’s and women’s interest in and hypothetical reactions to working for tech companies with different male:female staff ratios (either 3:1 or 1:1). Participants were asked to imagine applying for, obtaining, then commencing a project management position in the tech industry. At the application stage, they were shown recruitment materials that contained images of male and female staff in either a 3:1 or a 1:1 ratio (depending on which condition they had been randomized to). 

Later, when participants imagined starting the project management role, they were told that the on-the-ground (actual) staff ratio that they witnessed on their first day at work was either a 3:1 or a 1:1 male:female staff ratio (again depending on which condition they had been randomized to). 

The researchers assessed the perceived sincerity of the organization by asking participants two questions about the perceived sincerity of the company’s interest in improving gender diversity. They assessed identity threat by averaging the responses from six questions that asked participants the degree to which they would be concerned about being left out or stereotyped, not respected, or not having their opinion or contributions valued due to their gender.

The researchers then used multicategorical conditional process analysis (explained below) to show that:

1. The perceived sincerity (of a company’s interest in increasing gender diversity) mediates the relationship between on-the-ground gender diversity and identify threat concerns – and this mediation relationship is moderated by participant gender; and
2. The perceived sincerity (of a company’s interest in increasing gender diversity) also mediates the relationship between on-the-ground diversity and company interest post-measurements – and this mediation relationship is also moderated by participant gender. 

What participation involved

To see what the study involved, you can preview it. In summary, once a given participant provided informed consent:

1. They were randomized into one of four different conditions. The four different conditions are listed in the next section. 
2. They were shown three company site images about a project manager position in the technology industry. The content of the images depended on the condition to which they were assigned. Some participants saw a company that looks “gender diverse,” with a 50:50 gender split. Others see a company that appears to have a 3:1 male:female staff ratio.
3. They were asked their level of interest in the project manager position at the company and were asked a series of questions about the images they reviewed. Questions associated with this part of the experiment were labeled as “T1” variables.
4. They were asked to imagine obtaining and starting the project manager role at the technology company. They were told about the ratio of men to women observed during their first day on the job. Depending on the condition to which they have been randomized, some participants were told the actual ratio of men to women observed on their first day is 1:1, while others were instead told the ratio of men to women is 3:1. 
5. They were again asked their level of interest in the project manager position at the company and were asked a series of questions about the gender ratio that they have just been told about.
6. Participants were also asked how “sincerely interested” in gender diversity the company seems to be. They were then presented with a series of identity threat questions, an attention check, and a question about their gender.

Perceived sincerity

The authors included this variable because they suspected that it would mediate the relationships between experimental conditions and both identity threat and company interest. The authors defined “perceived sincerity” as the average of the responses to the following two questions:

• To what extent do you think Harrison Technologies is sincerely interested in increasing gender diversity in their workforce? [Rated from “Not at all sincere”, 1, to “Extremely sincere”, 5]
• How believable is Harrison Technologies’ interest in increasing gender diversity in their workforce? [Rated from “Not at all believable”, 1, to “Extremely believable”, 5]

Identity threat

This was one of the key outcome variables in the experiment. The authors defined identity threat concerns as the average of the responses to the following six questions (which were rated from “Not at all”, 1, to “An extreme amount”, 5):

• How much might you worry that you won’t belong at the company?
• How much might you worry that you cannot be your true self at the company?
• How much might you worry about being left out or marginalized at the company?
• How much might you worry about being stereotyped because of your gender at the company?
• How much might you worry that others will not respect you at the company?
• How much might you worry that others will not value your opinion or contributions at the company?

Company/position interest

Participants’ interest in the hypothetical project manager position after they found out about the ratio of male to female staff on their first day at work (“Interest_T2”) was one of the key outcome variables in the experiment. 

The authors defined Interest_T1 as the answer to the following question (which was asked after participants saw the company ad):

1. Imagine that you are looking for a project manager position in the tech industry and you encountered the job advertisement on the Harrison Technologies’ website. How interested would you be in the project manager position at Harrison Technologies? [Rated from “Not at all,” 1, to “Extremely interested,” 5]

The authors defined Interest_T2 as the answer to the following question (which was asked after participants had been told about their hypothetical first day at work):

2. After your first day on the job, how interested would you be in the project manager position at Harrison Technologies? [Rated from “Not at all,” 1, to “Extremely interested,” 5]

Diversity expectations

Diversity expectations were used for a manipulation check. The authors defined the diversity expectation variable (“diversityExpectation”) at time point 1 (“xDiversityExpecationT1”) as the average of the responses to the following two statements (which were rated from “Strongly Disagree”, 1, to “Strongly Agree”, 7):

• I expect Harrison Technologies to be *gender diverse.*
• I expect to find a *predominantly male* workforce at Harrison Technologies. [Scoring for this response was reversed.]

The authors defined the diversity expectation variable at time point 2 (“xDiversityExpecationT2”) the average of the responses to the following two statements (which were rated from “Strongly Disagree”, 1, to “Strongly Agree”, 7):

• After my first day of work at Harrison Technologies, I learned the company is *gender diverse.*
• After my first day of work at Harrison Technologies, I learned the company has a *predominantly male* workforce. [Scoring for this response was reversed

Conditional Process Analysis

For an explanation of the terms used in this section, please see Explanations of statistical terms in the appendices. The analysis used both in the original study and our replication is a so-called conditional process analysis, following Andrew Hayes’ PROCESS model. It is described in his book Introduction to Mediation, Moderation, and Conditional Process Analysis: A Regression-based Approach. Hayes lays out various different ways in which moderation and mediation can occur in the same model. If you aren’t familiar with the terminology in this section, please see the Glossary of Terms in the appendices.

A brief summary is given here of the particular model that the original study authors tested (known as “model 14”): in this model, there is: 

• An independent variable (which can be categorical, as in this study), 
• A dependent variable, 
• A mediator variable (that mediates the relationship between the independent and the dependent variable), and 
• A moderator variable (that, in this particular model, moderates the relationship between the mediator variable and the dependent variable). 

These variables are shown below, along with the names that are traditionally given to the different “paths” in the model. 

In the diagram below…

• The “a” path (from the independent variables to the mediator variable) is quantified by finding the coefficient of the independent variable in a linear regression predicting the mediator variable. 
• The “b” and “c’ ” paths are quantified by finding the coefficients of the mediator and independent variables (respectively) in a regression involving the dependent variable as the outcome variable and all other relevant variables (the independent variable, the mediator variable, the moderator variable, and a mediator-moderator interaction term) as the predictor variables. 

In Hayes’ book, he states that mediation can be said to be occurring (within a given level of the moderator variable) as long as the indirect effect is different from zero – i.e., as long as the effect size of ab (i.e., the path from the independent variable to the dependent variable via the mediator variable) is different from zero. He states that the significance of the a and b paths on their own are not important, and that it is the product of the paths (ab) that determines whether the indirect effect can be said to be significant.

The “multicategorical” term used in the current study is referring to the fact that the independent variable is of a categorical nature (in this case, the different categories consisted of different contrasts between experimental conditions). 

Results from the Conditional Process Analysis

As mentioned above, in the original study, the researchers used multicategorical conditional process analysis to show that:

1. The perceived sincerity (of a company’s interest in increasing gender diversity) mediated the relationship between actual on-the-ground gender diversity and identify threat concerns – and this mediation relationship was moderated by participant gender. 

2. The perceived sincerity (of a company’s interest in increasing gender diversity) also mediated the relationship between on-the-ground diversity and company interest (measured at the end) – and this mediation relationship was also moderated by participant gender. 

Our replication

To replicate this study, we used the same methods described above, and undertook the same analyses as those described above. Many thanks to the original study team for reviewing our replication materials prior to the study being run. As per our pre-registration document, our main aim here was to see if we could reproduce our own version of the original study’s results figures (labeled as Figures 8 and 9 in the original paper), but as we explain later, these were not the only (and arguably were not the most important) results relevant to our replication attempt. 

We ran our experiment via GuidedTrack.com and recruited study participants on Positly.com. The original study had a total of 505 U.S. adults (after accounting for exclusions) and our study had a similar total (523 U.S. adults after accounting for exclusions). In both the original and our replication, all participants were either male or female (and approximately 50% were female; those who were non-binary or who did not reveal their gender were excluded).

To experience our replication study as study participants saw it, click here. The images and scenario that you are given will change across multiple repetitions of the preview.

Experimental conditions

As in the original experiment, participants were randomly assigned to one of four conditions, listed below (with a probability of 0.25 of going to any one of the four conditions). 

Condition 0 = Authentically Diverse: participants in this condition were…

1. Shown company site images with a 50:50 gender split (i.e., they see an equal number of men and women featured on the Harrison Technologies website)
2. Told that the gender split on the ground on their first day is again 3:1 men:women 

Condition 1 = Aspirational Diversity: participants in this condition were…

1. Shown company site images with a 3:1 male:female gender ratio 
2. Told that the gender split on the ground on their first day is 3:1 men:women
3. Given a statement from top company executives stating that the company isn’t yet where it wants to be in terms of gender diversity, but that they’re working toward increasing gender diversity in the future

Condition 2 = Authentic NonDiversity: participants in this condition were…

1. Shown company site images with a 3:1 male:female gender ratio 
2. Told that the gender split on the ground on their first day is 3:1 men:women

Condition 3 = Counterfeit Diversity: participants in this condition were…

1. Shown company site images with a 50:50 gender split
2. Told that the gender split on the ground on their first day is 3:1 men:women 

Detailed Results

The results are summarized below, but you can find a more detailed overview in the appendices. The findings that we aimed to reproduce are shown in Figures 8 and 9 in the original paper (copied below). 

Figure 8 in the original paper illustrated how identity threat concerns were affected by the different diversity conditions (listed above) and perceived “sincerity” levels (as measured in this survey). Below is a copy of the original figure, with the numbers we derived from our data added in colored (green and dark red) writing beside the original study’s numbers.

Figure 9 in the original paper illustrated how the reported level of interest in a project manager position at a hypothetical tech company were affected by the different diversity conditions (explained above) and perceived “sincerity” levels (as measured in this study). Furthermore, in the original study, the relationship between “sincerity” and the aforementioned interest levels was moderated by gender, but this was not the case in our replication. Below is a copy of the original figure, with the numbers we derived from our data added in colored (green and dark red) writing beside the original study’s numbers.

Across Figures 8 and 9 above, there are a total of 13 significant results (marked with asterisks) along the “a” and “b” paths combined (the c’ path is not the focus here), plus four significant results relating to the effects of gender. This gives a total of 17 significant results in the parts of the diagrams that are most relevant to the authors’ hypotheses. Of these 17 findings, 13 of them (76.5%) were replicated in our study.

The findings from the figures above are described in written form in the appendices.

Indirect Effects Results

One could argue that the results figures (above) do not show the most relevant results. According to the textbook that the authors cite (and that forms the main source of information on this analysis method):

“You absolutely should focus on the signs of a and b when talking about the indirect effect. Just don’t worry so much about p-values for these, because you care about ab, not a and b.” 

Depending on how one interprets this, the results recorded in supplementary tables S11 and S12 (in the supplementary material for the original paper) were arguably more important than the results shown in the figures, at least according to the textbook on conditional process analysis quoted above. (It may even be that Figures 8 and 9 could have potentially been relegated to the supplementary materials if needed.)

Indirect effects of experimental conditions on identity threat via “perceived sincerity”

In the original study, among female participants, the authors found significant indirect effects of each of the condition contrasts on identity threat concerns via “perceived sincerity.” We replicated all of those findings except for one: unlike the original study, we found no significant indirect effects of authentic non-diversity (compared to counterfeit diversity) on identity threat concerns via perceived sincerity.

Note that the original authorship team had also observed and reported on differences across studies regarding whether there were differences in the effects of authentic non-diversity compared to counterfeit diversity on identity threat concerns. More specifically, although they found a difference between these conditions in Study 3 (the focus of this replication), in Study 2 of their paper, they had found no such difference. They highlighted this in their paper. In the conclusion of their paper, they wrote: “Consistent with an active, dynamic construal process of situational cues, we found that authentically diverse companies were perceived to be the most sincerely interested in gender diversity, followed by aspirational diversity companies, and then followed by counterfeit diversity and authentic nondiversity companies—which usually did not differ from each other in engendering threat and lowering interest.” 

Within female participants, almost all experimental conditions had indirect effects on identity threat concerns via “perceived sincerity”…

Originally, there were significant indirect effects of…	on…	via…	Did we replicate this finding?
Aspirational Diversity compared to Authentic Diversity	identity threat concerns	“perceived sincerity”	✅
Authentic Non-Diversity compared to Authentic Diversity	identity threat concerns	“perceived sincerity”	✅
Counterfeit Diversity compared to Authentic Diversity	identity threat concerns	“perceived sincerity”	✅
Authentic Non-Diversity compared to Aspirational Diversity	identity threat concerns	“perceived sincerity”	✅
Counterfeit Diversity compared to Aspirational Diversity	identity threat concerns	“perceived sincerity”	✅
Authentic Non-Diversity compared to Counterfeit Diversity	identity threat concerns	“perceived sincerity”	❌

In the original study, the authors also found that gender significantly moderated the indirect effects of each of the condition contrasts on identity threat concerns via perceived sincerity. We again replicated all of those findings except one: in our data, gender did not significantly moderate the indirect effects of authentic non-diversity (compared to counterfeit diversity) on identity threat concerns via perceived sincerity (which is unsurprising, given these indirect effects weren’t significant in the first place). 

Within all participants…gender moderated experimental conditions’ indirect effects on identity threat concerns via “perceived sincerity”…

Originally, gender moderated the indirect effects of…	on…	via…	Did we replicate this finding?
Aspirational Diversity compared to Authentic Diversity	identity threat concerns	“perceived sincerity”	✅
Authentic Non-Diversity compared to Authentic Diversity	identity threat concerns	“perceived sincerity”	✅
Counterfeit Diversity compared to Authentic Diversity	identity threat concerns	“perceived sincerity”	✅
Authentic Non-Diversity compared to Aspirational Diversity	identity threat concerns	“perceived sincerity”	✅
Counterfeit Diversity compared to Aspirational Diversity	identity threat concerns	“perceived sincerity”	✅
Authentic Non-Diversity compared to Counterfeit Diversity	identity threat concerns	“perceived sincerity”	❌

Indirect effects of experimental conditions on job interest via “perceived sincerity”

In the original study, there were significant indirect effects of each condition contrast on job interest level at time point 2 via “perceived sincerity” (with job interest at time point 1 included as a covariate in this analysis). We replicated all of these findings, with one exception: unlike the original study, we found no significant indirect effects of authentic non-diversity (compared to counterfeit diversity) on company interest via perceived sincerity. Once again, however, note that the original authorship team had also observed and reported on differences across studies in the effects of authentic non-diversity compared to counterfeit diversity on company interest. As mentioned previously, in their conclusion, they wrote, “counterfeit diversity and authentic nondiversity companies… usually did not differ from each other in engendering threat and lowering interest.”

Within both male and female participants, almost all experimental conditions had indirect effects on interest at time point 2 (with interest at time point 1 entered as a covariate) via “perceived sincerity”…

Originally, there were significant indirect effects of…	on…	via…	Did we replicate this finding?
Aspirational Diversity compared to Authentic Diversity	company interest	“perceived sincerity”	✅
Authentic Non-Diversity compared to Authentic Diversity	company interest	“perceived sincerity”	✅
Counterfeit Diversity compared to Authentic Diversity	company interest	“perceived sincerity”	✅
Authentic Non-Diversity compared to Aspirational Diversity	company interest	“perceived sincerity”	✅
Counterfeit Diversity compared to Aspirational Diversity	company interest	“perceived sincerity”	✅
Authentic Non-Diversity compared to Counterfeit Diversity	company interest	“perceived sincerity”	❌

In the original study, the authors also found that gender significantly moderated the indirect effects of each of the condition contrasts on job interest at time point 2 via perceived sincerity. Unlike the original study, we found no evidence of gender moderating the indirect effects of diversity condition on company interest via sincerity perceptions (i.e., men and women did not differ in the degree to which the impact of diversity condition on company interest was mediated by “perceived sincerity” – the index of moderated mediation was not different from zero).

Within all participants, in the original study, gender mediated the experimental conditions’ indirect effects on interest at time point 2 (with interest at time point 1 entered as a covariate) via “perceived sincerity” – but in our replication, we found no such mediation by participant gender…

Originally, gender moderated the indirect effects of…	on…	via…	Did we replicate this finding?
Aspirational Diversity compared to Authentic Diversity	company interest	“perceived sincerity”	❌
Authentic Non-Diversity compared to Authentic Diversity	company interest	“perceived sincerity”	❌
Counterfeit Diversity compared to Authentic Diversity	company interest	“perceived sincerity”	❌
Authentic Non-Diversity compared to Aspirational Diversity	company interest	“perceived sincerity”	❌
Counterfeit Diversity compared to Aspirational Diversity	company interest	“perceived sincerity”	❌
Authentic Non-Diversity compared to Counterfeit Diversity	company interest	“perceived sincerity”	❌

Note that, in their original paper, the authorship team had highlighted how experiments 1 and 2 had not shown that gender moderated the indirect effects of diversity condition on company interest via perceived sincerity, while experiments 3 and 4 had. In their correspondence with us prior to data collection, the original authorship team again flagged this discrepancy between studies with us, and had correctly predicted that this moderation relationship might be less likely to replicate than others.

Summary of additional analyses

Manipulation check

As planned in our pre-registration, we also conducted a manipulation check (a repeated measures two-way analysis of variance [ANOVA] examining the effects of diversity condition and time point on the diversityExpectation variable), the results of which were significant (consistent with the manipulation having been successful) – see appendices for details. We note that, in both the original dataset and in ours, the diversityExpectation variable had kurtosis values exceeding 1 in magnitude; since non-normally distributed data presents a problem for ANOVAs, the original study authors had said (in their pre-registration) that skew or kurtosis values exceeding 1 in magnitude would lead them to conduct a transformation prior to conducting analyses, but they do not appear to have done that in their final paper.

Correlation between “perceived sincerity” and identity threat among women

As additional analyses outside of our replication, we also showed that, among women, “perceived sincerity” (with respect to interest in increasing gender diversity) was statistically significantly negatively correlated with identity threat concerns (Pearson’s r = -0.65, p = 1.78E-32).

Correlation between “perceived sincerity” and company interest

We also found that there was a statistically significant positive correlation between “perceived sincerity” (with respect to interest in increasing gender diversity) and interest in working for the company at the second time point, for both men (Pearson’s r = 0.51 , p = 1.4E-18) and women (Pearson’s r = 0.57, p = 7.2E-24).

We also conducted exploratory analyses – see the appendices for details of the additional analyses we conducted.

Interpreting the Results

The methods and results were explained quite transparently, but there would still be room for readers to misinterpret certain things. Areas where possible misinterpretations could arise are briefly described under headings below.

Interpretation of the study methods

Although the authors list their study methods and cite where further information can be found, readers would need to consult those external information sources in order to be sure to understand what the results are showing. The method chosen – conditional process analysis – is described in only a few places outside of the definitive textbook on the topic, which may limit the accessibility of methodological explanations for many readers. (In fact, this textbook, now in its third edition, appears to us to be the only definitive textbook describing the analysis method employed in this study. We were fortunate to have library access to the textbook to refer to for our study, but many potential readers would not have this.)

We acknowledge that it is common practice for authors to mention (or to very briefly describe) an analysis method without fully explaining it and/or by referring readers to other sources. However, we do think this point is nevertheless worth mentioning because it leaves room for readers to be more likely to misinterpret the findings of the study. 

Interpretation of the relative importance of different results

The only results figures for this study were Figures 8 and 9, which were shown earlier. However, as discussed above, according to the textbook on conditional process analysis, the combined indirect effect size (ab) is more important than the individual effect sizes (along the a and b paths individually). So, in order to stay aligned with the recommendations of the creator of the analysis method they used, it might have been advisable not to display those results figures in the main body of the text and to instead display them in supplementary materials. By placing them in the main body of the text, it may lead readers to believe that those findings are among the most important ones of the study.

Interpretation of the “sincerity” variable

It could be argued that the “sincerity” variable could have been labeled more precisely. If a reader were only to read the abstract or were only to read Figures 8 and 9, for example, they may not realize that “sincerity” was not referring to the perceived sincerity of the company in general, but was instead referring to the average of the responses to two questions that both related to the company’s sincere interest in increasing gender diversity. 

Sincerity, broadly construed, would not usually be assumed to mean sincere interest in increasing gender diversity. Consequently, some readers may be at risk of misinterpreting the mediation variable due to the broad label given to the “sincerity” variable. It would be unfortunate if some readers incorrectly interpreted the current study’s findings as being related to a more broadly-construed concept of sincerity (as opposed to the concept of perceived sincerity as defined in this particular paper).

Interpretation of “gender diversity”

Readers may infer that participants in the study knew what was meant by “increasing gender diversity” by the time they were asked how sincerely the company was in doing this, but this is debatable. Participants may have inferred the meaning of this term from the context in which they were reading it, but if they did not infer the meaning from the context, some may have wondered whether “gender diversity” was referring to a diverse range of different genders in the company, including non-binary genders (which is recognized elsewhere as a valid, though less common, interpretation of the phrase). 

Such an interpretation might give a (very) tentative explanation as to why male participants also appeared to report slightly more identity threat concerns in the less diverse workplace scenarios than the diverse workplace scenarios (rather than only female participants exhibiting this). Perhaps some assume (based on certain stereotypes surrounding ideas of “bro”/“dude culture”) that a workplace with predominantly men would be less understanding of different sexualities, and/or of non-conformity to traditional gender norms (and with respect to this latter point, it may be worth noting that even those who do identify as either male or female may not conform to traditional expectations in some ways).

Apart from those in the “Aspirational Diversity” condition, who were told that there was a statement from top company executives “about gender diversity” and were then given a statement that talked about increasing the representation of women at the company, no other arms of the experiment mentioned “gender diversity” until the questions were shown asking about the company’s sincere interest in increasing it. (This may not be a problem, but would complicate the interpretation of results if it turned out that participants in the other experiment arms did not know what was meant by “gender diversity.”)

Interpretation of “increasing gender diversity”

To gauge “sincerity,” participants were asked the degree to which Harrison Technologies is sincerely interested in increasing gender diversity in their workforce. Even if we assume that all participants had the same understanding of the phrase “gender diversity” (discussed above), the meaning of the phrase “increasing gender diversity” still leaves room for multiple possible interpretations. It could be argued that a workplace that already demonstrates a 50:50 gender split (within the subset of people who identify as having either one of the binary genders) cannot be more diverse than it already is (since any change in the proportion of men and women would then be making the workplace either predominantly male or predominantly female, and neither of those outcomes would be more “gender diverse” than a 50:50 split). This makes it difficult to interpret the meaning of “increasing gender diversity.” 

As alluded to earlier, other participants might have been imagining that “increasing gender diversity” would involve increasing the proportion of people in the workplace who identify as neither male nor female. If that was the interpretation, it would seem that participants’ responses were not only shaped by the balance of men and women at the company, but also whether they inferred the balance would give a clue as to whether the workplace would try to hire more people who identify as neither male nor female. 

This potential for different interpretations on the part of participants also translates into a potential interpretation difficulty for readers of this study. If participants in some conditions had varying ideas of what a sincere interest in “increasing gender diversity” entailed, then readers of this study would need to interpret results differently. More specifically, if participants were interpreting the idea of “increasing gender diversity” differently to how they were intended to interpret it, this would complicate our interpretations of all of the mediation relationships found in this study.

Conclusion 

We randomly selected a paper from a March JPSP journal, and within that paper, we focused on Study 3 because its findings appeared to be non-obvious in addition to being key to the authors’ overall conclusions. The study was described transparently in the paper and was feasible for us to accurately replicate using only publicly-available materials. This is a testament to the open science practices of the authors and JPSP. There were some minor points which required clarification prior to us running our replication study, and the authors were very helpful in answering our questions and ensuring that our study was a faithful replication of theirs. Our replication study had findings that were mostly consistent with the original study. One interesting difference was that, in our study, the indirect effects of diversity condition on company interest via “perceived sincerity” were not mediated by participant gender (unlike in the original study).

Notwithstanding the transparency and replicability of the original study, there were several aspects of the write-up that could have increased the probability that readers would misinterpret what was being shown or said. The main aspects we identified as potentially problematic were as follows:

• The analysis methods were described clearly in the paper, but were not explained. Instead, the authors referred to a textbook, which we later found out is the only definitive resource on the analysis method employed in this study.
  • We acknowledge that it is common practice for authors to mention an analysis method without fully explaining it and by referring readers to other sources. However, we do think it is worth mentioning because it leaves room for readers to be more likely to misinterpret the findings of the study.
• Several terms were used when describing results that could reasonably be interpreted as meaning something different to what they actually meant, and readers would only have identified this problem if they had read the scales used (by referring to the supplementary materials).
• If participants in the study had understood the idea of “increasing gender diversity” in a different way to how it was intended to be understood, this would complicate our interpretation of all of the mediation relationships found in this study.

Purpose of Transparent Replications by Clearer Thinking

Transparent Replications conducts replications and evaluates the transparency of randomly-selected, recently-published psychology papers in prestigious journals, with the overall aim of rewarding best practices and shifting incentives in social science toward more replicable research.

We welcome reader feedback on this report, and input on this project overall.

Author Acknowledgements

The original study team gave us prompt and helpful feedback which greatly improved the quality of our replication. The authors also provided helpful feedback on an earlier draft of this report. (However, the responsibility for the contents of the report remains with the author and the rest of the Transparent Replications team.)

Many thanks also go to Spencer Greenberg and Amanda Metskas for their feedback throughout the study process and for their input on earlier drafts of this report. Thank you to Nikos Bosse for helping to post about the study on Metaculus, and to our Ethics Evaluator for their time reviewing the study before we ran it. Last but certainly not least, many thanks to our participants for their time and attention.

Appendices

Additional Information about the Ratings

Expanding on the Transparency Ratings

1. Methods transparency (5 stars):

1-a: The methods and publicly-accessible materials described the administration of the study in enough detail for us to be able to replicate the original study accurately. Consequently, we gave the highest possible rating for this sub-criterion.

1-b: The scales used were publicly available and were easy to find within the OSF materials. Consequently, we gave the highest possible rating for this sub-criterion.

2. Analysis Transparency (4.5 stars):

The authors were very transparent about the analysis methods they used and readily communicated with us about them in response to our questions. They lost half a star because one of the SPSS files on the OSF site for the project listed an incorrect model number which would have resulted in different results to those shown in the manuscript. However, this was considered to be a relatively minor oversight – it was easy for us to find because the model had been recorded accurately in the body of the paper.

3. Data availability (5 stars):  

All data were publicly available and were easy to find on the OSF project site. Consequently, we gave the highest possible rating for this criterion.

4. Pre-registration (2.5 stars):

In summary, the authors pre-registered the study, but there were some deviations from this pre-registration, as well as a set of analyses (that formed the main focus of the discussion and conclusions for this study) that were not mentioned in the pre-registration.

In the body of the paper, the “identity threat composite” score was calculated differently to how it had been planned in the pre-registration, but this deviation was acknowledged in a footnote, and the pre-registered version of the score was still calculated in the supplementary materials.

However, there were also deviations that were not acknowledged in the paper:

• In the paper, perceptions of company sincerity were measured by averaging two items together: “To what extent do you think Harrison Technologies is sincerely interested in increasing gender diversity in their workforce?” and “How believable is Harrison Technologies’ interest in increasing gender diversity in their workforce?”
  • In the pre-registration, the plan had been to average the response to three questions instead of two (the third one being: “How committed do you think the company is to increasing gender diversity in their workforce?”) but this was not mentioned in the body of the paper.
• In the paper, multicategorical conditional process analysis was the main analysis method chosen and reported upon for Study 3; their findings formed the basis of the discussion and conclusions for this study.
  • In the pre-registration, however, multicategorical conditional process analysis was not mentioned in either the main analysis section nor the exploratory analysis section.
• In the pre-registration, the “main analyses” that had been planned had been a series of  repeated measures two-way ANOVAs. These were replaced with conditional process analysis in the final paper, but the fact that this decision was made was not explicitly mentioned or explained in the paper.
  • The manipulation check that was reported upon in the paper was listed as one of these two-way ANOVAs. However, they had also listed the following point about their ANOVAs in their pre-registration (but did not report acting on this in their paper):
    • “If our data are non-normally distributed, we will conduct either a square-root, logarithmic, or inverse transformation—depending on the severity of the non-normality. If these transformations do not improve normality, we will use equivalent tests that do not require data to be normally distributed.”

Explanations of statistical terms

The analysis conducted in the paper was a multicategorical conditional process analysis. This glossary is designed to help you navigate the explanations in the event that there are any terms that are unfamiliar to you. 

Glossary of terms

Please skip this section if you are already familiar with the terms, and if this is the first time you are reading about any of these concepts, please note that the definitions given are (sometimes over-)simplifications.

• Independent variable (a.k.a. predictor variable): a variable in an experiment or study that is altered or measured, and which affects other (dependent) variables. [In many studies, including this one, we don’t know whether an independent variable is actually influencing the dependent variables, so calling it a “predictor” variable may not be warranted, but many models implicitly assume that this is the case. The term “predictor” variable is used here because it may be more familiar to readers.] 
• Dependent variable (a.k.a. outcome variable): a variable that is influenced by an independent variable. [In many studies, including this one, we don’t know whether a dependent variable is actually being causally influenced by the independent variables, but many models implicitly assume that this is the case.] 
• Null Hypothesis: in studies investigating the possibility of a relationship between given pairs/sets of variables, the Null Hypothesis assumes that there is no relationship between those variables.
• P-values: the p-value of a result quantifies the probability that a result at least as extreme as that result would have been observed if the Null Hypothesis were true. All p-values fall in the range (0, 1].
• Statistical significance: by convention, a result is deemed to be statistically significant if the p-value is below 0.05, meaning that there is a 5% chance that a result at least as extreme as that result would have occurred if the Null Hypothesis were true.
  • The more statistical tests conducted in a particular study, the more likely it is that some results will be statistically significant due to chance. So, when multiple statistical tests are performed in the same study, many argue that one should correct for multiple comparisons.
  • Statistical significance also does not necessarily translate into real-world/clinical/practical significance – to evaluate that, you need to know about the effect size as well.
• Linear regression: this is a process for predicting levels of a dependent/outcome variable (often called a y variable) based on different levels of an independent/predictor variable (often called an x variable), using an equation of the form y = mx + c (where m is the rate at which the dependent/outcome variable changes as a function of changes in the independent/predictor variable, and c describes the level of the dependent variable that would be expected if the independent/predictor variable, x, was set to a level of 0).
• Mediator variable: a variable which (at least partly) explains the relationship between a predictor variable and an outcome variable. [Definitions of moderation vary, but Andrew Hayes defines it as occurring any time when an indirect effect – i.e., the effect of a predictor variable on the outcome variable via the mediator variable, is statistically significantly different from zero.]
• Moderator variable: a variable which changes the strength or direction of a relationship between a predictor variable and an outcome variable. 
• Categorical variables: these are variables described in terms of categories (as opposed to being described in terms of a continuous scale).
• Reference category for multicategorical x variables in regressions: this is the category against which the effects of other categories are compared. The reference category is not included as one of the predictor variables – instead, all the other categories are included as predictor variables (and their effects are compared against the one that is left out).
  • In order to model the effects of a categorical variable on an outcome variable, you need to have something to compare the categorical variable to. When there are only two, mutually-exclusive categories (i.e., when you are working with a dichotomous predictor variable), this is relatively easy – you just model the effects of one category in comparison to the absence of that category (which equates to comparing one category to the other). The category you are comparing to is called the reference category. If you want to model the effects of the variable you used as the reference category, you just switch the variables around so that the other variable is the reference category.
  • For categorical variables with more than two categories (e.g., let’s say you have three categories, called I, II, and III), you end up needing to do multiple regressions before you can quantify the effects of all of the variables in comparison to all the others. You first choose one category as the reference or comparison category (e.g., variable I), then you can quantify the effects of the others (in comparison to that reference category; e.g., quantify the effects of variables II and III in comparison to variable I). In order to quantify all the effects of all the variables, you then need to switch the variables around so that you’re also running regressions with each other variable (in turn) as the reference category (e.g., quantifying the effects of variables I and III with variable II as the reference category, then quantifying the effects of variables I and II with variable III as the reference category).

Additional Information about the Results

Figures 8 and 9 from the original study described in sentences

Here is a list of the original study’s significant results in Figure 8 above, but this time in word format:

• If we use a linear regression to predict perceived sincerity (the y variable) using three categorical x variables (all with authentic diversity set as the reference category) – aspirational diversity, authentic non-diversity, and counterfeit diversity – then…
  • …the coefficient of the aspirational diversity (versus authentic diversity) contrast is statistically significantly different from 0 (p <0.001), at a value of -0.74. 
  • …the coefficient of the authentic non-diversity (versus authentic diversity) contrast is statistically significantly different from 0 (p <0.001), at a value of -1.56. 
  • …the coefficient of the counterfeit diversity (versus authentic diversity) contrast is statistically significantly different from 0 (p <0.001), at a value of -1.30. 
• If we use a linear regression to predict perceived sincerity (the y variable) using three categorical x variables (all with aspirational diversity set as the reference category) – authentic diversity, authentic non-diversity, and counterfeit diversity – then…
  • …the coefficient of the authentic non-diversity (versus aspirational diversity) contrast is statistically significantly different from 0 (p <0.001), at a value of -0.82. 
  • …the coefficient of the counterfeit diversity (versus aspirational diversity) contrast is statistically significantly different from 0 (p <0.001), at a value of -0.56. 
• If we use a linear regression to predict perceived sincerity (the y variable) using three categorical x variables (all with counterfeit diversity set as the reference category) – aspirational diversity, authentic non-diversity, and authentic diversity – then…
  • …the coefficient of the authentic non-diversity (versus aspirational diversity) contrast is statistically significantly different from 0 (p <0.05), at a value of -0.26. 
• If we use a linear regression to predict identity threat concerns (the y variable) using perceived sincerity as one of the predictors, gender as another predictor, the interaction between gender and sincerity as another predictor, and three categorical x variables (all with authentic diversity set as the reference category) – aspirational diversity, authentic non-diversity, and counterfeit diversity – as categorical predictors, then…
  • ……the coefficient of the aspirational diversity (versus authentic diversity) contrast is statistically significantly different from 0 (p <0.001), at a value of 0.45. 
  • ….the coefficient of gender (with female gender coded as 1) is statistically significantly different from 0 (p <0.001), at a value of -2.09. 
  • ….the coefficient of the gender by sincerity interaction is statistically significantly different from 0 (p <0.001), at a value of -0.51. 
• If we use a linear regression to predict identity threat concerns (the y variable) using perceived sincerity as one of the predictors, gender as another predictor, the interaction between gender and sincerity as another predictor, and three categorical x variables (all with aspirational diversity set as the reference category) – authentic diversity, authentic non-diversity, and counterfeit diversity – as categorical predictors, then…
  • …the coefficient of the authentic non-diversity (versus aspirational diversity) contrast is statistically significantly different from 0 (p <0.05), at a value of -0.27. 
  • …the coefficient of the counterfeit diversity (versus aspirational diversity) contrast is statistically significantly different from 0 (p <0.01), at a value of -0.32. 

Here is a list of the original study’s significant results in Figure 9 above, but this time in word format:

• If we use a linear regression to predict perceived sincerity (the y variable) using three categorical x variables (all with authentic diversity set as the reference category) – aspirational diversity, authentic non-diversity, and counterfeit diversity – and using baseline interest level as a covariate – then…
  • …the coefficient of the aspirational diversity (versus authentic diversity) contrast is statistically significantly different from 0 (p <0.001), at a value of -0.77. 
  • …the coefficient of the authentic non-diversity (versus authentic diversity) contrast is statistically significantly different from 0 (p <0.001), at a value of -1.57. 
  • …the coefficient of the counterfeit diversity (versus authentic diversity) contrast is statistically significantly different from 0 (p <0.001), at a value of -1.32. 
• If we use a linear regression to predict perceived sincerity (the y variable) using three categorical x variables (all with aspirational diversity set as the reference category) – authentic diversity, authentic non-diversity, and counterfeit diversity – then…
  • …the coefficient of the authentic non-diversity (versus aspirational diversity) contrast is statistically significantly different from 0 (p <0.001), at a value of -0.80. 
  • …the coefficient of the counterfeit diversity (versus aspirational diversity) contrast is statistically significantly different from 0 (p <0.001), at a value of -0.55. 
• If we use a linear regression to predict perceived sincerity (the y variable) using three categorical x variables (all with counterfeit diversity set as the reference category) – aspirational diversity, authentic non-diversity, and authentic diversity – then…
  • …the coefficient of the authentic non-diversity (versus aspirational diversity) contrast is statistically significantly different from 0 (p <0.05), at a value of -0.24. 
• If we use a linear regression to predict company interest (the y variable) using perceived sincerity as one of the predictors, gender as another predictor, the interaction between gender and sincerity as another predictor, and three categorical x variables (all with authentic diversity set as the reference category) – aspirational diversity, authentic non-diversity, and counterfeit diversity – as categorical predictors, and using baseline interest level as a covariate, then…
  • …the coefficient of perceived sincerity is statistically significantly different from 0 (p <0.001), at a value of 0.25. 
  • ….the coefficient of gender (with female gender coded as 1) is statistically significantly different from 0 (p <0.01), at a value of -0.61. 
  • ….the coefficient of the gender by sincerity interaction is statistically significantly different from 0 (p <0.05), at a value of 0.17. 

How we defined the “percentage of findings that replicated” in this study

Our current policy for calculating the percentage of findings that replicate in a given study is as follows. (This policy may change over time, but the policy below is what applied when we replicated this particular study.)

1. We currently limit ourselves to the findings that are reported upon in the body of a paper. (In other words, we do not base our calculations on supplementary or other findings that aren’t recorded in the body of the paper.)
2. Within the findings in the paper, we select the ones that were presented by the authors as being key results of the study that we are replicating.
   1. If there is a key results table or figure, we include that in the set of main results to consider.
   2. If a manipulation check is included in the study results, we also conduct that, but we do not count toward the denominator of “total number of findings” when calculating the percentage of findings that replicate.
   3. We pre-register the set of hypotheses that we consider to be the “main” ones we are testing.
3. Within the set of findings that we focus on, we only count the ones that were reported to be statistically significant in the original paper. That is, we do not count a null result in the original paper as a finding that contributes to the denominator (when calculating the percentage that replicate).

In this paper, we were focusing on Study 3, and the main findings for that study (as presented in the body of the paper) are shown in Figures 8 and 9. Other findings are also recorded, but these related to the manipulation check and so were only pre-registered as secondary analyses and were not the main focus of our analyses (nor did they contribute to the denominator when calculating the percentage of findings that replicated).

Within Figures 8 and 9, we focused on paths a and b, plus the gender-related interaction terms, as these were most relevant to the authors’ hypotheses. However, we did not count non-significant findings in the original study and instead focused on the significant findings among the a and b paths and gender effects. There were a total of 17 significant results (along the a and b paths and gender effects, across Figures 8 to 9).

A possible problem with how we’re calculating the replication rate in this paper

We are continuing to follow our pre-registered plan, but it seems worth highlighting a potential problem with this in the case of this particular study (also noted in the body of our write-up). According to the textbook that the authors cite (and that forms the main source of information on this analysis method):

“You absolutely should focus on the signs of a and b when talking about the indirect effect. Just don’t worry so much about p-values for these, because you care about ab, not a and b.” 

Depending on how one interprets this, it may be that the supplementary tables of indirect effects and indices of moderated mediation would have been well-placed in the main body of the paper (with Figures 8 and 9 being potentially relegated to the supplementary materials if needed).

We may have done some things differently if we weren’t aiming for an exact replication of findings reported in the body of the paper

As noted above, we should probably have reported on the main results differently and would have relegated Figures 8 and 9 to the supplementary materials. In addition, we probably would not have done the ANOVAs given the non-normally distributed data we observed (unless we had done some kind of transformation of the data first).

Conditional process analysis results in more detail

Reproduction of Figure 8 – with commentary

Below is Figure 8 from the original paper, with our findings written in dark green and red font alongside the original findings. 

There are a few different ways to quantify the replication rate of the findings in this paper. As explained above, we have chosen to focus on the findings in the diagram that were most relevant to the original authors’ hypotheses and that were significant in the original paper. This translated into counting the significant findings in the diagram except for the c’ paths (which were not as relevant to the hypotheses the authors were investigating, given that they were using Hayes’ conditional process analysis to investigate them – Hayes explicitly states in his textbook that mediation can be said to be occurring even if the c’ path is significant). Of the eight significant results (excluding the c’ paths) in this diagram, seven of them replicated in our study (87.5%). Here are some of the other ways we could quantify the replication rate:

• Out of the 15 numbers here, the number that successfully replicated (in the sense that our result matched the direction and significance [or non-significance] of their original finding) was 13 (~87%).  (There was one finding they had that was significant which didn’t replicate, and one finding they had that was non-significant which was significant in ours – these are shown as dark red numbers in the image below.) 
• If we ignore the b path (which was non-significant in the first instance and then significant in our replication), of the 14 remaining numbers in the diagram, 13 of them replicated (~93%).

Reproduction of Figure 9 – with commentary

Below is Figure 9 from the original paper, with our findings written in dark green and red font alongside the original findings. Of the nine significant results (excluding the c’ paths) in this diagram, six of them replicated in our study (66.7%). The differences in findings were as follows:

• In our study, it appears the effects of counterfeit diversity and authentic non-diversity were very similar to each other (whereas in the original, authentic non-diversity had appeared to be perceived as less sincerely interested in increasing gender diversity than counterfeit diversity). 
• We found no evidence of gender influencing company interest or interacting with perceived sincerity. 

Here is another way we could quantify the replication rate:

• Out of the 15 numbers here (including the c’ paths), the number that successfully replicated (in the sense that our result matched the direction and significance [or non-significance] of their original finding) was 12 (80%). 

Reproduction of Supplementary Table S11

Indirect effects: Diversity condition -> xSincerity -> xThreatBasedConcerns

Unlike the original study, we found no significant indirect effects of authentic non-diversity (compared to counterfeit diversity) on identity threat concerns via perceived sincerity. Other findings, however, were successfully replicated in our study.

Indirect effects for female participants – from the original study and our replication

In the table below, findings that we replicated are displayed in green font, and the finding that we did not replicate is displayed in dark red font.

Indirect effects for male participants – from the original study and our replication

In the table below, the (null) finding that we replicated is displayed in green font, and the findings that were non-significant in the original study, but significant in our study, are displayed in dark orange font.

Index of moderated mediation 

Unlike the original study, we found that gender did not appear to significantly moderate the  indirect effects of authentic non-diversity (compared to counterfeit diversity) on identity threat concerns via perceived sincerity (which is unsurprising, given these indirect effects weren’t significant in the first place, as shown in the previous table). That non-replicated finding is displayed in dark red font. Other findings, however (shown in green font), were successfully replicated in our study.

For comparison: Original S11

Reproduction of Supplementary Table S12

Indirect effects: Diversity condition -> xSincerity -> Interest_T2

Unlike the original study, we found no significant indirect effects of authentic non-diversity (compared to counterfeit diversity) on company interest via perceived sincerity. Other findings, however, were successfully replicated in our study.

Indirect effects for female participants – from the original study and our replication

Indirect effects for male participants – from the original study and our replication

Index of moderated mediation 

Unlike the original study, we found no evidence of gender moderating the indirect effects of diversity condition on company interest via sincerity perceptions (i.e., men and women did not differ in the degree to which the impact of diversity condition on company interest was mediated by perceived sincerity – the index of moderated mediation was not different from zero).

For comparison: Original S12

Manipulation check details

As per our pre-registered plan, a two-way analysis of variance (ANOVA) was performed to assess the effects of diversity condition and time point on diversity expectations. This was performed in Jasp (which is worth noting as there may be different results in Jasp versus SPSS: Jasp runs on R code, and ANOVAs have been observed to return different results in R versus SPSS, at least in previous years). 

Note that the data are kurtotic in both the original data set (-1.25) and in our replication (-1.27). The study authors had originally planned to do a transformation on the dataset if this occurred, but they did not report having done so in their paper. We aimed to replicate their methods exactly, and had pre-registered our intention to do this manipulation check in the way outlined above, so we did not perform a transformation on the dataset either.

We found that the kurtosis of the diversityExpectation variable (with time point 1 and time point 2 pooled) was -1.25 (standard error: 0.15) for the original dataset. This was also evident on visual inspection of the original diversityExpectation data (pooled across time points 1 and 2), which is clearly not normally distributed, as shown below. (Confirming our visual observations, the Shapiro-Wilk test was significant (9.02E-23).)

Similar to the original data, our diversityExpectation data was also kurtotic (kurtosis -1.27 [standard error: 0.15]). However, we still employed this method because (1) this is what we pre-registered and (2) we were aiming to replicate the methods of the original study exactly. 

Like in the original study, the results were significant (i.e., were consistent with the manipulation check having worked). More specifically, in a repeated measures ANOVA, with diversity condition and gender as between-subjects factors and diversityExpectation as the repeated-measures factor, there were statistically significant main effects of time (F(1,515) = 784.39, p = 1.44E-105) and diversity condition (F(3,515) = 357.78, p = 3.06E-129), as well as a significant interaction between time and diversity condition (F(3,515) = 299.72, p = 1.57E-112).

Additional Analyses

The first two analyses discussed below were also included in the body of the text, but are included again here for those who want to review all the additional, non-replication-related analyses in one place.

Pre-registered additional analyses

Correlation between “perceived sincerity” and identity threat among women

As additional analyses outside of our replication, we also showed that, among women, “perceived sincerity” (with respect to interest in increasing gender diversity) was statistically significantly negatively correlated with identity threat concerns (Pearson’s r = -0.65, p = 1.78E-32). (This was also the case for men, but we did not pre-register this, and the identity threat concerns among men were lower across all conditions than they were for women.) 

Correlation between “perceived sincerity” and company interest

We also found that there was a statistically significant positive correlation between “perceived sincerity” (with respect to interest in increasing gender diversity) and interest in working for the company at the second time point, for both men (Pearson’s r = 0.51 , p = 1.4E-18) and women (Pearson’s r = 0.57, p = 7.2E-24).

Comment on correlations

One might argue that including the correlations above could have served to highlight some of the conclusions described in the paper, but in a way that would have been more accessible and intuitive for a wider range of audiences to understand. However, these simpler analyses don’t show that “perceived sincerity” was mediating the relationship between experimental conditions and the two main outcome variables, so it would have been insufficient on its own in demonstrating the findings from this paper.

Exploratory additional analyses

As we mentioned in our pre-registration, we also planned to conduct exploratory analyses. Our exploratory analyses are reported upon below. For anyone reading this, if you have any suggestions for additional exploratory  analyses for us to run, please let us know.

For a company with a 3:1 male:female staff ratio, it probably doesn’t actually harm “perceived sincerity” to misrepresent gender diversity in company ads (compared to showing ads with 3:1 ratio and saying nothing about it), but it would be even better to show ads with a 3:1 ratio and to follow up with a statement about diversity (as in the “aspirational diversity” condition in this experiment)

Comparing “perceived sincerity” between counterfeit diversity and authentic non-diversity

You might ask, if your company has a 3:1 ratio of men to women, is it worse (in terms of the “perceived sincerity” outcome of this experiment) to present your ads with a 50:50 gender split, compared to just showing ads with a 3:1 ratio (i.e., is it worse to make it look like you’re more diverse than you are, rather than just showing things as they are, if your goal is to convince the audience that you are sincerely interested in increasing gender diversity in your workplace)? The answer appears to be no, at least according to this Mann-Whitney U test (which we performed instead of a student’s t-test as data were non-normally distributed). The mean “perceived sincerity” in the counterfeit diversity condition (2.22) was no different to the mean in the authentically non-diverse condition (2.22; Mann-Whitney U = 8380, n1 = 143, n2 = 119, p = 0.83).

Comparing “perceived sincerity” between counterfeit diversity and aspirational diversity

You might ask, if your company has a 3:1 ratio of men to women, can you get better results (in terms of the “perceived sincerity” outcome of this experiment) by showing ads with a 3:1 ratio if you also include a statement about the importance of increasing gender diversity, compared to if you showed ads with 50:50 split without addressing the gender ratio? In other words, if your goal is to convince the audience that you are sincerely interested in increasing gender diversity in your workplace, would you be better off presenting things as they are plus writing a statement about your intentions to improve gender diversity (as opposed to being better off presenting ads with a 50:50 gender split)? The answer here appears to be yes – it seems to be better to present things as they are while highlighting how important it is to the company executives to improve the company’s gender diversity (at least compared to simply showing a 50:50 image split without any accompanying statement about diversity). The mean “perceived sincerity” for the aspirational diversity condition (3.04) was significantly greater than the mean for the counterfeit diversity condition (2.22; Mann-Whitney U = 11369, n1 = 107, n2 = 143, p = 1.78E-11).

Comments on “perceived sincerity” in the conditions above

Taking the above two results together, if someone was trying to design promotional materials for a tech company with a 3:1 male:female staff ratio, and if their goal was to convince their audience that their workplace was sincerely interested in increasing gender diversity, they would be better off including images with a 50:50 split than doing nothing, but an even better option (with respect to their stated goal) would be to include a realistic 3:1 split in the images but to also present the audience with a statement from company executives explaining that they recognize a problem and that they aspire to increase gender diversity.

For companies with a 3:1 male:female staff ratio, it probably doesn’t cause more identity threat concerns among women if they misrepresent gender diversity in company ads – there are likely going to be similar levels of identity threat concerns in that scenario compared to the other two tested presentations in this experiment

Comparing identity threat concerns between counterfeit diversity and authentic non-diversity – for women participants

You might ask, if your company has a 3:1 ratio of men to women, is it worse (in terms of the identity threats reported by women in this experiment after day 1 at work) to present your ads with a 50:50 gender split, compared to just showing ads with a 3:1 ratio? In other words, is it worse to make it look like you’re more diverse than you are, rather than just showing things as they are, if your goal is to minimize identity threat concerns experienced by women after day 1 at your workplace? The answer appears to be no. The mean level of identity threat concerns reported by women in the counterfeit diversity condition (2.75) was no different to the mean in the authentically non-diverse condition (2.74; Mann-Whitney U = 2279, n1 = 71, n2 = 65, p = 0.96).

Comparing identity threat concerns between counterfeit diversity and aspirational diversity – for women participants

You might ask, if your company has a 3:1 ratio of men to women, can you get better results (i.e., fewer identity threats reported by women in this experiment after day 1 at work) by showing ads with a 3:1 ratio if you also include a statement about the importance of increasing gender diversity, compared to if you showed ads with 50:50 split without addressing the gender ratio? In other words, if your goal is to minimize identity threat concerns experienced by women working at your organization after their first day of work, would you be better off presenting things as they are plus writing a statement about your intentions to improve gender diversity (as opposed to being better off presenting ads with a 50:50 gender split)? The answer is probably no. The mean level of identity threat concerns reported by women in the aspirational diversity condition (2.63) was not significantly smaller than the mean in the counterfeit diversity condition (2.75; Mann-Whitney U = 1525, n1 = 47, n2 = 71, p = 0.43).

Comments on identity threat concerns among women in the conditions above

Taking the above two results together, if someone was trying to design promotional materials for a tech company with a 3:1 male:female staff ratio, and if their goal was to minimize the extent to which new women employees experienced identity threat concerns, neither of the attempted approaches explored in this experiment (presenting 50:50 gender split and presenting a 3:1 split but including a company statement about the importance of gender diversity) appear to be helpful in reducing identity threat concerns.

Comparing company interest between counterfeit diversity and authentic non-diversity – for all participants

You might ask, if your company has a 3:1 ratio of men to women, is it worse (in terms of the level of interest that people have in continuing to work for your organization after day 1) to present your ads with a 50:50 gender split, compared to just showing ads with a 3:1 ratio? In other words, is it worse to make it look like you’re more diverse than you are, rather than just showing things as they are, if your goal is to have people interested in continuing to work for you after day 1 of work? The answer appears to be no. The mean level of interest at time point 2 in the counterfeit diversity condition (3.51) was not significantly higher than the mean in the authentically non-diverse condition (3.40; Mann-Whitney U = 7989.5, n1 = 143, n2 = 119, p = 0.38).

Comparing company interest between aspirational diversity and counterfeit diversity – for all participants

You might ask, if your company has a 3:1 ratio of men to women, can you get better results (in terms of the level of interest that people have in continuing to work for your organization after day 1) by showing ads with a 3:1 ratio if you also include a statement about the importance of increasing gender diversity, compared to if you showed ads with 50:50 split without addressing the gender ratio? In other words, if your goal is to maximize the level of interest that people have in continuing to work for your organization after day 1, would you be better off presenting things as they are plus writing a statement about your intentions to improve gender diversity (as opposed to being better off presenting ads with a 50:50 gender split)? The answer looks like a no (although there was a trend toward a yes). The mean level of interest in the aspirational diversity condition (3.75) was not statistically significantly greater than the mean in the counterfeit diversity condition (3.51; Mann-Whitney U = 8605.5, n1 = 107, n2 = 143, p = 0.07).

Comments on identity threat concerns among women in the conditions above

Taking these results together, it appears that a company with a 3:1 ratio of men to women won’t be able to significantly increase the interest people have in continuing to work there simply by creating ads with a 50:50 gender split or by having a statement about the importance of improving gender diversity in their workplace (although the latter showed a non-significant trend toward being useful).

A condition not included in the experiment 

Something that has not been addressed by this experiment is the possible effects of presenting ads (for non-diverse companies) with a 50:50 gender split, in addition to a statement by company executives about how the company is actually not where they want to be in terms of gender balance and about how much the company executives prioritize the goal of increasing the company’s gender diversity. It would be interesting to see if it would be helpful (in terms of identity threat concerns and in terms of company interest) to show a 50:50 gender split in company ads, then to also show a statement about the company’s commitment to improving the actual gender diversity among their staff (similar to the “aspirational diversity” condition, except in this case preceded by ads with a 50:50 gender split).

References

Hayes, A. F. (2022). Introduction to mediation, moderation, and conditional process analysis a regression-based approach (Third edition.). The Guilford Press.

Kroeper, K. M., Williams, H. E., & Murphy, M. C. (2022). Counterfeit diversity: How strategically misrepresenting gender diversity dampens organizations’ perceived sincerity and elevates women’s identity threat concerns. Journal of Personality and Social Psychology, 122(3), 399-426. https://doi.org/10.1037/pspi0000348