Category Archives: Replicability

Replicability Report for the Journal ‘Evolutionary Psychology’

Publication Bias, Replicability, Replicability Rankings, ,

Authors: Maria Soto and Ulrich Schimmack

Citation: Soto, M. & Schimmack, U. (2024, June, 24/06/24).  2024 Replicability Report for the Journal 'Evolutionary Psychology'.  Replicability Index. 
https://replicationindex.com/2024/06/24/rr24-evopsy/

Introduction

In the 2010s, it became apparent that empirical psychology had a replication problem. When psychologists tested the replicability of 100 results, they found that only 36% of the 97 significant results in original studies could be reproduced (Open Science Collaboration, 2015). In addition, several prominent cases of research fraud further undermined trust in published results. Over the past decade, several proposals were made to improve the credibility of psychology as a science. Replicability Reports aim to improve the credibilty of psychological science by examining the amount of publication bias and the strength of evidence for empirical claims in psychology journals.

The main problem in psychological science is the selective publishing of statistically significant results and the blind trust in statistically significant results as evidence for researchers’ theoretical claims. Unfortunately, psychologists have been unable to self-regulate their behaviour and continue to use unscientific practices to hide evidence that disconfirms their predictions. Moreover, ethical researchers who do not use unscientific practices are at a disadvantage in a game that rewards publishing many articles without concern about these findings’ replicability.

My colleagues and I have developed a statistical tool that can reveal the use of unscientific practices and predict the outcome of replication studies (Brunner & Schimmack, 2021; Bartos & Schimmack, 2022). This method is called z-curve. Z-curve cannot be used to evaluate the credibility of a single study. However, it can provide valuable information about the research practices in a particular research domain.

Replicability-Reports (RR) use z-curve to provide information about psychological journal research and publication practices. This information can aid authors choose journals they want to publish in, provide feedback to journal editors who influence selection bias and replicability of published results, and, most importantly, to readers of these journals.

Evolutionary Psychology

Evolutionary Psychology was founded in 2003. The journal focuses on publishing empirical theoretical and review articles investigating human behaviour from an evolutionary perspective. On average, Evolutionary Psychology publishes about 35 articles in 4 annual issues.

As a whole, evolutionary psychology has produced both highly robust and questionable results. Robust results have been found for sex differences in behaviors and attitudes related to sexuality. Questionable results have been reported for changes in women’s attitudes and behaviors as a function of hormonal changes throughout their menstrual cycle.

According to Web of Science, the impact factor of Evolutionary Psychology ranks 88th in the Experimental Psychology category (Clarivate, 2024). The journal has a 48 H-Index (i.e., 48 articles have received 48 or more citations).

In its lifetime, Evolutionary Psychology has published over 800 articles The average citation rate in this journal is 13.76 citations per article. So far, the journal’s most cited article has been cited 210 times. The article was published in 2008 and investigated the influence of women’s mate value on standards for a long-term mate (Buss & Shackelford, 2008).

The current Editor-in-Chief is Professor Todd K. Shackelford. Additionally, the journal has four other co-editors Dr. Bernhard Fink, Professor Mhairi Gibson, Professor Rose McDermott, and Professor David A. Puts.

Extraction Method

Replication reports are based on automatically extracted test statistics such as F-tests, t-tests, z-tests, and chi2-tests. Additionally, we extracted 95% confidence intervals of odds ratios and regression coefficients. The test statistics were extracted from collected PDF files using a custom R-code. The code relies on the pdftools R package (Ooms, 2024) to render all textboxes from a PDF file into character strings. Once converted the code proceeds to systematically extract the test statistics of interest (Soto & Schimmack, 2024). PDF files identified as editorials, review papers and meta-analyses were excluded. Meta-analyses were excluded to avoid the inclusion of test statistics that were not originally published in Evolution & Human Behavior. Following extraction, the test statistics are converted into absolute z-scores.

Results For All Years

Figure 1 shows a z-curve plot for all articles from 2003-2023 (see Schimmack, 2023, for a detailed description of z-curve plots). However, the total available test statistics available for 2003, 2004 and 2005 were too low to be used individually. Therefore, these years were joined to ensure the plot had enough test statistics for each year. The plot is essentially a histogram of all test statistics converted into absolute z-scores (i.e., the direction of an effect is ignored). Z-scores can be interpreted as the strength of evidence against the null hypothesis that there is no statistical relationship between two variables (i.e., the effect size is zero and the expected z-score is zero). A z-curve plot shows the standard criterion of statistical significance (alpha = .05, z = 1.96) as a vertical red dotted line.

Figure 1

Z-curve plots are limited to values less than z = 6. The reason is that values greater than 6 are so extreme that a successful replication is all but certain unless the value is a computational error or based on fraudulent data. The extreme values are still used for the computation of z-curve statistics but omitted from the plot to highlight the shape of the distribution for diagnostic z-scores in the range from 2 to 6. Using the expectation maximization (EM) algorithm, Z-curve estimates the optimal weights for seven components located at z-values of 0, 1, …. 6 to fit the observed statistically significant z-scores. The predicted distribution is shown as a blue curve. Importantly, the model is fitted to the significant z-scores, but the model predicts the distribution of non-significant results. This makes it possible to examine publication bias (i.e., selective publishing of significant results). Using the estimated distribution of non-significant and significant results, z-curve provides an estimate of the expected discovery rate (EDR); that is, the percentage of significant results that were actually obtained without selection for significance. Using Soric’s (1989) formula the EDR is used to estimate the false discovery risk; that is, the maximum number of significant results that are false positives (i.e., the null-hypothesis is true).

Selection for Significance

The extent of selection bias in a journal can be quantified by comparing the Observed Discovery Rate (ODR) of 68%, 95%CI = 67% to 70% with the Expected Discovery Rate (EDR) of 49%, 95%CI = 26%-63%. The ODR is higher than the upper limit of the confidence interval for the EDR, suggesting the presence of selection for publication. Even though the distance between the ODR and the EDR estimate is narrower than those commonly seen in other journals the present results may underestimate the severity of the problem. This is because the analysis is based on all statistical results. Selection bias is even more problematic for focal hypothesis tests and the ODR for focal tests in psychology journals is often close to 90%.

Expected Replication Rate

The Expected Replication Rate (ERR) estimates the percentage of studies that would produce a significant result again if exact replications with the same sample size were conducted. A comparison of the ERR with the outcome of actual replication studies shows that the ERR is higher than the actual replication rate (Schimmack, 2020). Several factors can explain this discrepancy, such as the difficulty of conducting exact replication studies. Thus, the ERR is an optimist estimate. A conservative estimate is the EDR. The EDR predicts replication outcomes if significance testing does not favour studies with higher power (larger effects and smaller sampling error) because statistical tricks make it just as likely that studies with low power are published. We suggest using the EDR and ERR in combination to estimate the actual replication rate.

The ERR estimate of 72%, 95%CI = 67% to 77%, suggests that the majority of results should produce a statistically significant, p < .05, result again in exact replication studies. However, the EDR of 49% implies that there is some uncertainty about the actual replication rate for studies in this journal and that the success rate can be anywhere between 49% and 72%.

False Positive Risk

The replication crisis has led to concerns that many or even most published results are false positives (i.e., the true effect size is zero). Using Soric’s formula (1989), the maximum false discovery rate can be calculated based on the EDR.

The EDR of 49% implies a False Discovery Risk (FDR) of 6%, 95%CI = 3% to 15%, but the 95%CI of the FDR allows for up to 15% false positive results. This estimate contradicts claims that most published results are false (Ioannidis, 2005).

Changes Over Time

One advantage of automatically extracted test-statistics is that the large number of test statistics makes it possible to examine changes in publication practices over time. We were particularly interested in changes in response to awareness about the replication crisis in recent years.

Z-curve plots for every publication year were calculated to examine time trends through regression analysis. Additionally, the degrees of freedom used in F-tests and t-tests were used as a metric of sample size to observe if these changed over time. Both linear and quadratic trends were considered. The quadratic term was included to observe if any changes occurred in response to the replication crisis. That is, there may have been no changes from 2000 to 2015, but increases in EDR and ERR after 2015.

Degrees of Freedom

Figure 2 shows the median and mean degrees of freedom used in F-tests and t-tests reported in Evolutionary Psychology. The mean results are highly variable due to a few studies with extremely large sample sizes. Thus, we focus on the median to examine time trends. The median degrees of freedom over time was 121.54, ranging from 75 to 373. Regression analyses of the median showed a significant linear increase by 6 degrees of freedom per year, b = 6.08, SE = 2.57, p = 0.031. However, there was no evidence that the replication crisis influenced a significant increase in sample sizes as seen by the lack of a significant non-linear trend and a small regression coefficient, b = 0.46, SE = 0.53, p = 0.400.

Figure 2

Observed and Expected Discovery Rates

Figure 3 shows the changes in the ODR and EDR estimates over time. There were no significant linear, b = -0.52 (SE = 0.26 p = 0.063) or non-linear, b = -0.02 (SE = 0.05, p = 0.765) trends observed in the ODR estimate. The regression results for the EDR estimate showed no significant linear, b = -0.66 (SE = 0.64 p = 0.317) or non-linear, b = 0.03 (SE = 0.13 p = 0.847) changes over time. These findings indicate the journal has not increased its publication of non-significant results and continues to report more significant results than one would predict based on the mean power of studies.

Expected Replicability Rates and False Discovery Risks

Figure 4 depicts the false discovery risk (FDR) and the Estimated Replication Rate (ERR). It also shows the Expected Replication Failure rate (EFR = 1 – ERR). A comparison of the EFR with the FDR provides information for the interpretation of replication failures. If the FDR is close to the EFR, many replication failures may be due to false positive results in original studies. In contrast, if the FDR is low, most replication failures will likely be false negative results in underpowered replication studies.

The ERR estimate did not show a significant linear increase over time, b = 0.36, SE = 0.24, p = 0.165. Additionally, no significant non-linear trend was observed, b = -0.03, SE = 0.05, p = 0.523. These findings suggest the increase in sample sizes did not contribute to a statistically significant increase in the power of the published results. These results suggests that replicability of results in this journal has not increased over time and that the results in Figure 1 can be applied to all years.

Figure 4

Visual inspection of Figure 4 depicts the EFR between 30% and 40% and an FDR between 0 and 10%. This suggests that more than half of replication failures are likely to be false negatives in replication studies with the same sample sizes rather than false positive results in the original studies. Studies with large sample sizes and small confidence intervals are needed to distinguish between these two alternative explanations for replication failures.

Adjusting Alpha

A simple solution to a crisis of confidence in published results is to adjust the criterion to reject the null-hypothesis. For example, some researchers have proposed to set alpha to .005 to avoid too many false positive results. With z-curve we can calibrate alpha to keep the false discovery risk at an acceptable level without discarding too many true positive results. To do so, we set alpha to .05, .01, .005, and .001 and examined the false discovery risk.

Figure 5

Figure 5 shows that the conventional criterion of p < .05 produces false discovery risks above 5%. The high variability in annual estimates also makes it difficult to provide precise estimates of the FDR. However, adjusting alpha to .01 is sufficient to produce an FDR with tight confidence intervals below 5%. The benefits of reducing alpha further to .005 or .001 are minimal.

Figure 6

Figure 6 shows the impact of lowering the significance criterion, alpha, on the discovery rate (lower alpha implies fewer significant results). In Evolutionary Psychology lowering alpha to .01 reduces the observed discovery rate by about 20 to 10 percentage points. This implies that 20% of results reported p-values between .05 and .01. These results often have low success rates in actual replication studies (OSC, 2015). Thus, our recommendation is to set alpha to .01 to reduce the false positive risk to 5% and to disregard studies with weak evidence against the null-hypothesis. These studies require actual successful replications with larger samples to provide credible evidence for an evolutionary hypothesis.

There are relatively few studies with p-values between .01 and .005. Thus, more conservative researchers can use alpha = .005 without losing too many additional results.

Limitations

The main limitation of these results is the use of automatically extracted test statistics. This approach cannot distinguish between theoretically important statistical results and other results that are often reported but do not test focal hypotheses (e.g., testing the statistical significance of a manipulation check, reporting a non-significant result for a factor in a complex statistical design that was not expected to produce a significant result).

To examine the influence of automatic extraction on our results, we can compare the results to hand-coding results of over 4,000 hand-coded focal hypotheses in over 40 journals in 2010 and 2020. The ODR was 90% around 2010 and 88% around 2020. Thus, the tendency to report significant results for focal hypothesis tests is even higher than the ODR for all results and there is no indication that this bias has decreased notably over time. The ERR increased a bit from 61% to 67%, but these values are a bit lower than those reported here. Thus, it is possible that focal tests also have lower average power than other tests, but this difference seems to be small. The main finding is that the publishing of non-significant results for focal tests remains an exception in psychology journals and probably also in this journal.

One concern about the publication of our results is that it merely creates a new criterion to game publications. Rather than trying to get p-values below .05, researchers may use tricks to get p-values below .01. However, this argument ignores that it becomes increasingly harder to produce lower p-values with tricks (Simmons et al., 2011). Moreover, z-curve analysis makes it easy to see selection bias for different levels of significance. Thus, a more plausible response to these results is that researchers will increase sample sizes or use other methods to reduce sampling error to increase power.

Conclusion

The replicability report shows that the average power to report a significant result (i.e., a discovery) ranges from 49% to 72% in Evolutionary Psychology. This finding is higher than previous estimates observed in evolutionary psychology journals. However, the confidence intervals are wide and suggest that many published studies remain underpowered. The report did not capture any significant changes over time in the power and replicability as captured by the EDR and the ERR estimates. The false positive risk is modest and can be controlled by setting alpha to .01. Replication attempts of original findings with p-values above .01 should increase sample sizes to produce more conclusive evidence. Lastly, the journal shows clear evidence of selection bias.

There are several ways, the current or future editors of this journal can improve the credibility of results published in this journal. First, results with weak evidence (p-values between .05 and .01) should only be reported as suggestive results that require replication or even request a replication before publication. Second, editors should try to reduce publication bias by prioritizing research questions over results. A well-conducted study with an important question should be published even if the results are not statistically significant. Pre-registration and registered reports can help to reduce publication bias. Editors may also ask for follow-up studies with higher power to follow up on a non-significant result.

Publication bias also implies that point estimates of effect sizes are inflated. It is therefore important to take uncertainty in these estimates into account. Small samples with large sampling errors are usually unable to provide meaningful information about effect sizes and conclusions should be limited to the direction of an effect.

The present results serve as a benchmark for future years to track progress in this journal to ensure trust in research by evolutionary psychologists.

Replicability Reports of Psychology Journals – 2024

Publication Bias, Replicability, Replicability-Report

Citation: Soto, M. & Schimmack, U. (2024, July 5, 2024). Replicability Report of Psychology Journals – 2024. Replicability Index.
https://replicationindex.com/2024/07/05/replicability-reports-of-psychology-journals/

In the 2010s, it became apparent that empirical psychology has a replication problem. When psychologists tested the replicability of 100 results, they found that only 36% of the 97 significant results in original studies could be reproduced (Open Science Collaboration, 2015). In addition, several prominent cases of research fraud further undermined trust in published results. Over the past decade, several proposals were made to improve the credibility of psychology as a science. Replicability reports are the results of one of these initiatives.

The main problem in psychological science is the selective publishing of statistically significant results and the blind trust in statistically significant results as evidence for researchers’ theoretical claims. Unfortunately, psychologists have been unable to self-regulate their behavior and continue to use unscientific practices to hide evidence that disconfirms their predictions. Moreover, ethical researchers who do not use unscientific practices are at a disadvantage in a game that rewards publishing many articles without any concern about the replicability of these findings.

My colleagues and I have developed a statistical tools that can reveal the use of unscientific practices and predict the outcome of replication studies (Brunner & Schimmack, 2021; Bartos & Schimmack, 2022). This method is called z-curve. Z-curve cannot be used to evaluate the credibility of a single study. However, it can provide valuable information about the research practices in a particular research domain.

Research reports use z-curve to provide information about psychological journals. This information can be used by authors to chose journals they want to publish in, provides feedback to journal editors who have influence on selection bias and replicability of results published in their journals, and most importantly to readers of these journals.

List of Journals with Replicability Reports for 2024

Acta Psychologica (2000-2023)

Evolution and Human Behavior (2000-2023)

Evolutionary Psychology (2000-2023)

Journal of Experimental Social Psychology (2000-2023)

Replicability Report 2024: Acta Psychologica

Replicability, Replicability Report, , ,

Authors: Maria Soto and Ulrich Schimmack

Citation: Soto, M. & Schimmack, U. (2024, July 4/06/24).  2024 Replicability Report for the Journal 'Acta Psychologica'.  Replicability Index. 
https://replicationindex.com/2024/07/04/rr24-actapsy/

Introduction

In the 2010s, it became apparent that empirical psychology had a replication problem. When psychologists tested the replicability of 100 results, they found that only 36% of the 97 significant results in original studies could be reproduced (Open Science Collaboration, 2015). In addition, several prominent cases of research fraud further undermined trust in published results. Over the past decade, several proposals were made to improve the credibility of psychology as a science. Replicability Reports aim to improve the credibility of psychological science by examining the amount of publication bias and the strength of evidence for empirical claims in psychology journals.

The main problem in psychological science is the selective publishing of statistically significant results and the blind trust in statistically significant results as evidence for researchers’ theoretical claims. Unfortunately, psychologists have been unable to self-regulate their behavior and continue to use unscientific practices to hide evidence that disconfirms their predictions. Moreover, ethical researchers who do not use unscientific practices are at a disadvantage in a game that rewards publishing many articles without any concern about the replicability of these findings.

My colleagues and I have developed a statistical tools that can reveal the use of unscientific practices and predict the outcome of replication studies (Brunner & Schimmack, 2021; Bartos & Schimmack, 2022). This method is called z-curve. Z-curve cannot be used to evaluate the credibility of a single study. However, it can provide valuable information about the research practices in a particular research domain. Replicability-Reports (RR) analyze the statistical results reported in a journal with z-curve to estimate the replicability of published results, the amount of publication bias, and the risk that significant results are false positive results (i.e, the sign of a mean difference or correlation of a significant result does not match the sign in the population).

Acta Psychologica

Acta Psychologica is an old psychological journal that was founded in 1936. The journal publishes articles from various areas of psychology, but cognitive psychological research seems to be the most common area. Since 2021, the journal is a Gold Open Access journal that charges authors a $2,000 publication fee.

On average, Acta Psychologica publishes about 150 articles a year in 9 annual issues.

According to Web of Science, the impact factor of Acta Psychologica ranks 44th in the Experimental Psychology category (Clarivate, 2024). The journal has an H-Index of 140 (i.e., 140 articles have received 140 or more citations).

In its lifetime, Acta Psychologica has published over 6,000 articles with an average citation rate of 21.5 citations. So far, the journal has published 5 articles with more than 1,000 citations. However, most of these articles were published in the 1960s and 1970s.  The most highly cited article published in the 2000s examined the influence of response categories on the psychometric properties of survey items (Preston & Colman, 2000; 1055 citations).

Psychology literature has faced difficult realizations in the last decade. Acta Psychologica is a broad-scope journal that offers us the possibility to observe changes in the robustness of psychological research practices and results. The current report serves as a glimpse into overall trends in psychology literature as it considers research from multiple subfields.

Given the multidisciplinary nature of the journal, the journal has a team of editors. The current editors are Dr. Muhammad Abbas, Dr. Mohamed Alansari, Dr. Colin Cooper, Dr. Valerie De Cristofaro, Dr. Nerelie Freeman, Professor, Alessandro Gabbiadini, Professor Matthieu Guitton, Dr. Nhung T Hendy, Dr. Amanpreet Kaur, Dr. Shengjie Lin, Dr. Hui Jing Lu, Professor Robrecht Van Der Wel and Dr. Olvier Weigelt.

Extraction Method

Replication reports are based on automatically extracted test statistics such as F-tests, t-tests, z-tests, and chi2-tests. Additionally, we extracted 95% confidence intervals of odds ratios and regression coefficients. The test statistics were extracted from collected PDF files using a custom R-code. The code relies on the pdftools R package (Ooms, 2024) to render all textboxes from a PDF file into character strings. Once converted the code proceeds to systematically extract the test statistics of interest (Soto & Schimmack, 2024). PDF files identified as editorials, review papers and meta-analyses were excluded. Meta-analyses were excluded to avoid the inclusion of test statistics that were not originally published in Acta Psychologica Following extraction, the test statistics are converted into absolute z-scores.

Results For All Years

Figure 1 shows a z-curve plot for all articles from 2000-2023 (see Schimmack, 2022a, 2022b, for a detailed description of z-curve plots). The plot is essentially a histogram of all test statistics converted into absolute z-scores (i.e., the direction of an effect is ignored). Z-scores can be interpreted as the strength of evidence against the null hypothesis that there is no statistical relationship between two variables (i.e., the effect size is zero and the expected z-score is zero). A z-curve plot shows the standard criterion of statistical significance (alpha = .05, z = 1.96) as a vertical red dotted line.

Figure 1

Z-curve plots are limited to values less than z = 6. The reason is that values greater than 6 are so extreme that a successful replication is all but certain unless the value is a computational error or based on fraudulent data. The extreme values are still used for the computation of z-curve statistics but omitted from the plot to highlight the shape of the distribution for diagnostic z-scores in the range from 2 to 6. Using the expectation maximization (EM) algorithm, Z-curve estimates the optimal weights for seven components located at z-values of 0, 1, …. 6 to fit the observed statistically significant z-scores. The predicted distribution is shown as a blue curve. Importantly, the model is fitted to the significant z-scores, but the model predicts the distribution of non-significant results. This makes it possible to examine publication bias (i.e., selective publishing of significant results). Using the estimated distribution of non-significant and significant results, z-curve provides an estimate of the expected discovery rate (EDR); that is, the percentage of significant results that were actually obtained without selection for significance. Using Soric’s (1989) formula the EDR is used to estimate the false discovery risk; that is, the maximum number of significant results that are false positives (i.e., the null-hypothesis is true).

Selection for Significance

The extent of selection bias in a journal can be quantified by comparing the Observed Discovery Rate (ODR) of 70%, 95%CI = 70% to 71% with the Expected Discovery Rate (EDR) of 38%, 95%CI = 27%-54%. The ODR is notably higher than the upper limit of the confidence interval for the EDR, indicating statistically significant publication bias. It is noteworthy that the present results may underestimate the severity of the problem because the analysis is based on all statistical results. Selection bias is even more problematic for focal hypothesis tests and the ODR for focal tests in psychology journals is often higher than the ODR for all tests. Thus, the current results are a conservative estimate of bias for critical hypothesis tests.

Expected Replication Rate

The Expected Replication Rate (ERR) estimates the percentage of studies that would produce a significant result again if exact replications with the same sample size were conducted. A comparison of the ERR with the outcome of actual replication studies shows that the ERR is higher than the actual replication rate (Schimmack, 2020). Several factors can explain this discrepancy, including the difficulty of conducting exact replication studies. Thus, the ERR is an optimist estimate. A conservative estimate is the EDR. The EDR predicts replication outcomes if significance testing does not favour studies with higher power (larger effects and smaller sampling error) because statistical tricks make it just as likely that studies with low power are published. We suggest using the EDR and ERR in combination to estimate the actual replication rate.

The ERR estimate of 73%, 95%CI = 69% to 77%, suggests that the majority of results should produce a statistically significant, p < .05, result again in exact replication studies. However, the EDR of 38% implies that there is considerable uncertainty about the actual replication rate for studies in this journal and that the success rate can be anywhere between 27% and 77%.

False Positive Risk

The replication crisis has led to concerns that many or even most published results are false positives (i.e., the true effect size is zero or in the opposite direction). The high rate of replication failures, however, may simply reflect low power to produce significant results for true positives and does not tell us how many published results are false positives. We can provide some information about the false positive risk based on the EDR. Using Soric’s formula (1989), the EDR can be used to calculate the maximum false discovery rate.

The EDR of 38% for Acta Psychologica implies a False Discovery Risk (FDR) of 9%, 95%CI = 5% to 15%, but the 95%CI of the FDR allows for up to 15% false positive results. This estimate contradicts claims that most published results are false (Ioannidis, 2005), but is probably a bit higher than many readers of this journal would like.

Time Trends

One advantage of automatically extracted test-statistics is that the large number of test statistics makes it possible to examine changes in publication practices over time. We were particularly interested in changes in response to awareness about the replication crisis in recent years.

Z-curve plots for every publication year were calculated to examine time trends through regression analysis. Additionally, the degrees of freedom used in F-tests and t-tests were used as a metric of sample size to observe if these changed over time. Both linear and quadratic trends were considered. The quadratic term was included to observe if any changes occurred in response to the replication crisis. That is, there may have been no changes from 2000 to 2015 but increases in EDR and ERR after 2015.

Degrees of Freedom

Figure 2 shows the median and mean degrees of freedom used in F-tests and t-tests reported in Acta Psychologica. The mean results are highly variable due to a few studies with extremely large sample sizes. Thus, we focus on the median to examine time trends. The median degrees of freedom over time was 38, ranging from 22 to 74. Regression analyses of the median showed a significant linear increase of a 1.4 degrees of freedom per year, b = 1.39, SE = 3.00, p < 0.0001. Furthermore, the results suggest the replication crisis influenced a significant increase in sample sizes noted by the significant non-linear trend, b = 0.09, SE = 0.03, p = 0.007.

Figure 2

Observed and Expected Discovery Rates

Figure 3 shows the changes in the ODR and EDR estimates over time. The ODR estimate showed a significant linear decrease of about b = -0.42 (SE = 0.10 p = 0.001) percentage points per year.  The results did not show a significant non-linear trend in the ODR estimate, b = -0.10 (SE = 0.02, p = 0.563. The regression results for the EDR estimate showed no significant trends, linear, b = 0.04, SE = 0.37, p = 0.903, non-linear, b = 0.01, SE = 0.06, p = 0.906.

These findings indicate the journal has increased the publication of non-significant results. However, there is no evidence that this change occurred in response to the replicability crisis. Even with this change, the ODR and EDR estimates do not overlap, indicating that selection bias is still present. Furthermore, the lack of changes to the EDR suggests that many studies continue to be statistically underpowered to detect true effects.

Figure 3

Expected Replicability Rates and False Discovery Risks

Figure 4 depicts the false discovery risk (FDR) and the Estimated Replication Rate (ERR). It also shows the Expected Replication Failure rate (EFR = 1 – ERR). A comparison of the EFR with the FDR provides information for the interpretation of replication failures. If the FDR is close to the EFR, many replication failures may be due to false positive results in original studies. In contrast, if the FDR is low, most replication failures will likely be false negative results in underpowered replication studies.

There were no significant linear, b = 0.13, SE = 0.10, p = 0.204 or non-linear,  b = 0.01, SE = 0.16, p = 0.392 trends observed in the ERR estimate. These findings are inconsistent with the observed significant increase in sample sizes as the reduction in sampling error often increases the likelihood that an effect will replicate. One possible explanation for this is that the type of studies has changed. If a journal publishes more studies from disciplines with large samples and small effect sizes, sample sizes go up without increasing power.

Given the lack of change in the EDR and ERR estimate over time, many published significant results are based on underpowered studies that are difficult to replicate.

Figure 4

Visual inspection of Figure 4 depicts the EFR consistently around 30% and the FDR around 10%, suggesting that about 30% of replication failures are false positives.

Adjusting Alpha

A simple solution to a crisis of confidence in published results is to adjust the criterion to reject the null-hypothesis. For example, some researchers have proposed to set alpha to .005 to avoid too many false positive results. With z-curve, we can calibrate alpha to keep the false discovery risk at an acceptable level without discarding too many true positive results. To do so, we set alpha to .05, .01, .005, and .001 and examined the false discovery risk.

Figure 5

Figure 5 shows that the conventional criterion of p < .05 produces false discovery risks above 5%. The high variability in annual estimates also makes it difficult to provide precise estimates of the FDR. However, adjusting alpha to .01 is sufficient to produce an FDR with tight confidence intervals below 5%. The benefits of reducing alpha further to .005 or .001 are minimal.

Figure 6

Figure 6 shows the impact of lowering the significance criterion, alpha, on the discovery rate (lower alpha implies fewer significant results). In Acta Psychologica lowering alpha to .01 reduces the observed discovery rate by about 20 percentage points. This implies that 20% of results reported p-values between .05 and .01. These results often have low success rates in actual replication studies (OSC, 2015). Thus, our recommendation is to set alpha to .01 to reduce the false positive risk to 5% and to disregard studies with weak evidence against the null-hypothesis. These studies require actual successful replications with larger samples to provide credible evidence for an evolutionary hypothesis. There are relatively few studies with p-values between .01 and .005. Thus, more conservative researchers can use alpha = .005 without losing too many additional results.

Limitations

The main limitation of these results is the use of automatically extracted test statistics. This approach cannot distinguish between theoretically important statistical results and other results that are often reported but do not test focal hypotheses (e.g., testing the statistical significance of a manipulation check, reporting a non-significant result for a factor in a complex statistical design that was not expected to produce a significant result).

Hand-coding of 81 studies in 2010 and 112 studies from 2020 showed ODRs of 98%, 95%CI = 94%-100% and 91%, 95%CI = 86%-96%, suggesting a slight increase in reporting of non-significant focal tests. However, ODRs over 90% suggest that publication bias is still present in this journal. ERR estimates were similar and the small sample size made it impossible to obtain reliable estimates of the EDR and FDR.

One concern about the publication of our results is that it merely creates a new criterion to game publications. Rather than trying to get p-values below .05, researchers may use tricks to get p-values below .01. However, this argument ignores that it becomes increasingly harder to produce lower p-values with tricks (Simmons et al., 2011). Moreover, z-curve analysis makes it easy to see selection bias for different levels of significance. Thus, a more plausible response to these results is that researchers will increase sample sizes or use other methods to reduce sampling error to increase power.

Conclusion

The replicability report for Acta Psychologica shows clear evidence of selection bias, although there is a trend that selection bias has decreased due to reporting of more non-significant results, but not necessarily focal ones. The power to obtain a significant result to report a significant result (i.e., a discovery) ranges from 38% to 73%. This finding suggests that many studies are underpowered and require luck to get a significant result. The false positive risk is modest and can be controlled by setting alpha to .01. Replication attempts of original findings with p-values above .01 should increase sample sizes to produce more conclusive evidence.

There are several ways, the current or future editors of this journal can improve credibility of results published in this journal. First, results with weak evidence (p-values between .05 and .01) should only be reported as suggestive results that require replication or even request a replication before publication. Second, editors should try to reduce publication bias by prioritizing research questions over results. A well-conducted study with an important question should be published even if the results are not statistically significant. Pre-registration and registered reports can help to reduce publication bias. Editors may also ask for follow-up studies with higher power to follow up on a non-significant result.

Publication bias also implies that point estimates of effect sizes are inflated. It is therefore important to take uncertainty in these estimates into account. Small samples with large sampling errors are usually unable to provide meaningful information about effect sizes and conclusions should be limited to the direction of an effect.

We hope that these results provide readers of this journal with useful informatoin to evaluate the credibility of results reported in this journal. The results also provide a benchmark to evaluate the influence of reforms on the credibility of psychological science. We hope that reform initiatives will increase power and decrease publication bias and false positive risks.

2024 Replicability Report for the Journal ‘Evolution and Human Behavior’

Publication Bias, Replicability, Replicability Rankings, ,

Authors: Maria Soto and Ulrich Schimmack

Citation: Soto, M. & Schimmack, U. (2024, June, 24/06/24).  2024 Replicability Report for the Journal 'Evolution and Human Behavior'.  Replicability Index. 
https://replicationindex.com/2024/06/24/rr24-evohumbeh/

Introduction

In the 2010s, it became apparent that empirical psychology had a replication problem. When psychologists tested the replicability of 100 results, they found that only 36% of the 97 significant results in original studies could be reproduced (Open Science Collaboration, 2015). In addition, several prominent cases of research fraud further undermined trust in published results. Over the past decade, several proposals were made to improve the credibility of psychology as a science. Replicability Reports aim to improve the credibilty of psychological science by examining the amount of publication bias and the strength of evidence for empirical claims in psychology journals.

The main problem in psychological science is the selective publishing of statistically significant results and the blind trust in statistically significant results as evidence for researchers’ theoretical claims. Unfortunately, psychologists have been unable to self-regulate their behaviour and continue to use unscientific practices to hide evidence that disconfirms their predictions. Moreover, ethical researchers who do not use unscientific practices are at a disadvantage in a game that rewards publishing many articles without concern about these findings’ replicability.

My colleagues and I have developed a statistical tool that can reveal the use of unscientific practices and predict the outcome of replication studies (Brunner & Schimmack, 2021; Bartos & Schimmack, 2022). This method is called z-curve. Z-curve cannot be used to evaluate the credibility of a single study. However, it can provide valuable information about the research practices in a particular research domain.

Replicability-Reports (RR) use z-curve to provide information about psychological journal research and publication practices. This information can aid authors choose journals they want to publish in, provide feedback to journal editors who influence selection bias and replicability of published results, and, most importantly, to readers of these journals.

Evolution & Human Behavior

Evolution & Human Behavior is the official journal of the Human Behaviour and Evolution Society. It is an interdisciplinary journal founded in 1997. The journal publishes articles on human behaviour from an evolutionary perspective. On average, Evolution & Human Behavior publishes about 70 articles a year in 6 annual issues.

Evolutionary psychology has produced both highly robust and questionable results. Robust results have been found for sex differences in behaviors and attitudes related to sexuality. Questionable results have been reported for changes in women’s attitudes and behaviors as a function of hormonal changes throughout their menstrual cycle.

According to Web of Science, the impact factor of Evolution & Human Behaviour ranks 5th in the Behavioural Sciences category and 2nd in the Psychology, Biological category (Clarivate, 2024). The journal has an H-Index of 122 (i.e., 122 articles have received 122 or more citations).

In its lifetime, Evolution & Human Behavior has published over 1,400. Articles published by this journal have an average citation rate of 46.2 citations. So far, the journal has published 2 articles with more than 1,000 citations. The most highly cited article dates back to 2001 in which the authors argued that prestige evolved as a non-coercive social status to enhance the quality of “information goods” acquired via cultural transmission (Henrich & Gil-White, 2001).

The current Editor-in-Chief is Professor Debra Lieberman. The associate editors are Professor Greg Bryant, Professor Aaron Lukaszewski, and Professor David Puts.

Extraction Method

Replication reports are based on automatically extracted test statistics such as F-tests, t-tests, z-tests, and chi2-tests. Additionally, we extracted 95% confidence intervals of odds ratios and regression coefficients. The test statistics were extracted from collected PDF files using a custom R-code. The code relies on the pdftools R package (Ooms, 2024) to render all textboxes from a PDF file into character strings. Once converted the code proceeds to systematically extract the test statistics of interest (Soto & Schimmack, 2024). PDF files identified as editorials, review papers and meta-analyses were excluded. Meta-analyses were excluded to avoid the inclusion of test statistics that were not originally published in Evolution & Human Behavior. Following extraction, the test statistics are converted into absolute z-scores.

Results For All Years

Figure 1 shows a z-curve plot for all articles from 2000-2023 (see Schimmack, 2023, for a detailed description of z-curve plots). The plot is essentially a histogram of all test statistics converted into absolute z-scores (i.e., the direction of an effect is ignored). Z-scores can be interpreted as the strength of evidence against the null hypothesis that there is no statistical relationship between two variables (i.e., the effect size is zero and the expected z-score is zero). A z-curve plot shows the standard criterion of statistical significance (alpha = .05, z = 1.96) as a vertical red dotted line.

Figure 1

Z-curve plots are limited to values less than z = 6. The reason is that values greater than 6 are so extreme that a successful replication is all but certain unless the value is a computational error or based on fraudulent data. The extreme values are still used for the computation of z-curve statistics but omitted from the plot to highlight the shape of the distribution for diagnostic z-scores in the range from 2 to 6. Using the expectation maximization (EM) algorithm, Z-curve estimates the optimal weights for seven components located at z-values of 0, 1, …. 6 to fit the observed statistically significant z-scores. The predicted distribution is shown as a blue curve. Importantly, the model is fitted to the significant z-scores, but the model predicts the distribution of non-significant results. This makes it possible to examine publication bias (i.e., selective publishing of significant results). Using the estimated distribution of non-significant and significant results, z-curve provides an estimate of the expected discovery rate (EDR); that is, the percentage of significant results that were actually obtained without selection for significance. Using Soric’s (1989) formula the EDR is used to estimate the false discovery risk; that is, the maximum number of significant results that are false positives (i.e., the null-hypothesis is true).

Selection for Significance

The extent of selection bias in a journal can be quantified by comparing the Observed Discovery Rate (ODR) of 64%, 95%CI = 63% to 65% with the Expected Discovery Rate (EDR) of 28%, 95%CI = 17%-42%. The ODR is notably higher than the upper limit of the confidence interval for the EDR, indicating statistically significant publication bias. The ODR is also more than double than the point estimate of the EDR, indicating that publication bias is substantial. Thus, there is clear evidence of the common practice to omit reports of non-significant results. The present results may underestimate the severity of the problem because the analysis is based on all statistical results. Selection bias is even more problematic for focal hypothesis tests and the ODR for focal tests in psychology journals is often close to 90%.

Expected Replication Rate

The Expected Replication Rate (ERR) estimates the percentage of studies that would produce a significant result again if exact replications with the same sample size were conducted. A comparison of the ERR with the outcome of actual replication studies shows that the ERR is higher than the actual replication rate (Schimmack, 2020). Several factors can explain this discrepancy, such as the difficulty of conducting exact replication studies. Thus, the ERR is an optimist estimate. A conservative estimate is the EDR. The EDR predicts replication outcomes if significance testing does not favour studies with higher power (larger effects and smaller sampling error) because statistical tricks make it just as likely that studies with low power are published. We suggest using the EDR and ERR in combination to estimate the actual replication rate.

The ERR estimate of 71%, 95%CI = 66% to 77%, suggests that the majority of results should produce a statistically significant, p < .05, result again in exact replication studies. However, the EDR of 28% implies that there is considerable uncertainty about the actual replication rate for studies in this journal and that the success rate can be anywhere between 28% and 71%.

False Positive Risk

The replication crisis has led to concerns that many or even most published results are false positives (i.e., the true effect size is zero). Using Soric’s formula (1989), the maximum false discovery rate can be calculated based on the EDR.

The EDR of 28% implies a False Discovery Risk (FDR) of 14%, 95%CI = 7% to 26%, but the 95%CI of the FDR allows for up to 26% false positive results. This estimate contradicts claims that most published results are false (Ioannidis, 2005), but the results also create uncertainty about the credibility of results with statistically significant results, if up to 1 out of 4 results can be false positives.

Changes Over Time

One advantage of automatically extracted test-statistics is that the large number of test statistics makes it possible to examine changes in publication practices over time. We were particularly interested in changes in response to awareness about the replication crisis in recent years.

Z-curve plots for every publication year were calculated to examine time trends through regression analysis. Additionally, the degrees of freedom used in F-tests and t-tests were used as a metric of sample size to observe if these changed over time. Both linear and quadratic trends were considered. The quadratic term was included to observe if any changes occurred in response to the replication crisis. That is, there may have been no changes from 2000 to 2015, but increases in EDR and ERR after 2015.

Degrees of Freedom

Figure 2 shows the median and mean degrees of freedom used in F-tests and t-tests reported in Evolution & Human Behavior. The mean results are highly variable due to a few studies with extremely large sampel sizes. Thus, we focus on the median to examine time trends. The median degrees of freedom over time was 107.75, ranging from 54 to 395. Regression analyses of the median showed a significant linear increase by 4 to 5 degrees of freedom per year, b = 4.57, SE = 1.69, p = 0.013. However, there was no evidence that the replication crisis influenced a significant increase in sample sizes as seen by the lack of a significant non-linear trend and a small regression coefficient, b = 0.50, SE = 0.27, p = 0.082.

Figure 2

Observed and Expected Discovery Rates

Figure 3 shows the changes in the ODR and EDR estimates over time. There were no significant linear, b = 0.06 (SE = 0.17 p = 0.748) or non-linear,  b = -0.02 (SE = 0.03, p = 0.435) trends observed in the ODR estimate. The regression results for the EDR estimate showed no significant linear, b = 0.75 (SE = 0.51 p = 0.153) or non-linear, b = 0.04 (SE = 0.08 p = 0.630) changes over time. These findings indicate the journal has not increased its publication of non-significant results even though selection bias is heavily present. Furthermore, the lack of changes to the EDR suggests that many studies continue to be statistically underpowered to measure the effect sizes of interest.

Figure 3

Expected Replicability Rates and False Discovery Risks

Figure 4 depicts the false discovery risk (FDR) and the Estimated Replication Rate (ERR). It also shows the Expected Replication Failure rate (EFR = 1 – ERR). A comparison of the EFR with the FDR provides information for the interpretation of replication failures. If the FDR is close to the EFR, many replication failures may be due to false positive results in original studies. In contrast, if the FDR is low, most replication failures will likely be false negative results in underpowered replication studies.

The ERR estimate showed a significant linear increase over time, b = 0.61, SE = 0.26, p = 0.031. No significant non-linear trend was observed, b = 0.07, SE = 0.4, p = 0.127. These findings are consistent with the observed significant increase in sample sizes as the reduction in sampling error increases the likelihood that an effect will replicate.

The significant increase in the ERR without a significant increase in the EDR is partially explained by the higher power of the test for the ERR that can be estimated with higher precision. However, it is also possible that the ERR increases more because there is an increase in the heterogeneity of studies. That is, the number of studies with low power has remained constant, but the number of studies with high power has increased. This would result in a bigger increase in the ERR than the EDR.

Figure 4

Visual inspection of Figure 4 depicts the EFR higher than the FDR over time, suggesting that replication failures of studies in Evolution & Human Behavior are more likely to be false negatives rather than false positives. Up to 30% of the published results might not be replicable, and up to 50% of those results may be false positives.

It is noteworthy that the gap between the EFR and the FDR appears to be narrowing over time. This trend is supported by the significant increase in the Estimated Replicability Rate (ERR), where EFR is defined as 1 – ERR. Meanwhile, the Expected Discovery Rate (EDR) has remained constant, indicating that the FDR has also remained unchanged, given that the FDR is derived from a transformation of the EDR. The findings suggest that while original results have become more likely to replicate, the probability that replication failures are false positives remains unchanged.   

Adjusting Alpha

A simple solution to a crisis of confidence in published results is to adjust the criterion to reject the null-hypothesis. For example, some researchers have proposed to set alpha to .005 to avoid too many false positive results. With z-curve we can calibrate alpha to keep the false discovery risk at an acceptable level without discarding too many true positive results. To do so, we set alpha to .05, .01, .005, and .001 and examined the false discovery risk.

Figure 5

Figure 5 shows that the conventional criterion of p < .05 produces false discovery risks above 5%. The high variability in annual estimates also makes it difficult to provide precise estimates of the FDR. However, adjusting alpha to .01 is sufficient to produce an FDR with tight confidence intervals below 5%. The benefits of reducing alpha further to .005 or .001 are minimal.

Figure 6

Figure 6 shows the impact of lowering the significance criterion, alpha, on the discovery rate (lower alpha implies fewer significant results). In Evolution & Human Behavior lowering alpha to .01 reduces the observed discovery rate by about 20 percentage points. This implies that 20% of results reported p-values between .05 and .01. These results often have low success rates in actual replication studies (OSC, 2015). Thus, our recommendation is to set alpha to .01 to reduce the false positive risk to 5% and to disregard studies with weak evidence against the null-hypothesis. These studies require actual successful replications with larger samples to provide credible evidence for an evolutionary hypothesis.

There are relatively few studies with p-values between .01 and .005. Thus, more conservative researchers can use alpha = .005 without losing too many additional results.

Limitations

The main limitation of these results is the use of automatically extracted test statistics. This approach cannot distinguish between theoretically important statistical results and other results that are often reported but do not test focal hypotheses (e.g., testing the statistical significance of a manipulation check, reporting a non-significant result for a factor in a complex statistical design that was not expected to produce a significant result).

To examine the influence of automatic extraction on our results, we can compare the results to hand-coding results of over 4,000 hand-coded focal hypotheses in over 40 journals in 2010 and 2020. The ODR was 90% around 2010 and 88% around 2020. Thus, the tendency to report significant results for focal hypothesis tests is even higher than the ODR for all results and there is no indication that this bias has decreased notably over time. The ERR increased a bit from 61% to 67%, but these values are a bit lower than those reported here. Thus, it is possible that focal tests also have lower average power than other tests, but this difference seems to be small. The main finding is that publishing of non-significant results for focal tests remains an exception in psychology journals and probably also in this journal.

One concern about the publication of our results is that it merely creates a new criterion to game publications. Rather than trying to get p-values below .05, researchers may use tricks to get p-values below .01. However, this argument ignores that it becomes increasingly harder to produce lower p-values with tricks (Simmons et al., 2011). Moreover, z-curve analysis makes it easy to see selection bias for different levels of significance. Thus, a more plausible response to these results is that researchers will increase sample sizes or use other methods to reduce sampling error to increase power.

Conclusion

The replicability report for Evolution & Human Behavior suggests that the power to obtain a significant result to report a significant result (i.e., a discovery) ranges from 28% to 71%. This finding suggests that many studies are underpowered and require luck to get a significant result. The false positive risk is modest and can be controlled by setting alpha to .01. Replication attempts of original findings with p-values above .01 should increase sample sizes to produce more conclusive evidence. The journal shows clear evidence of selection bias.

There are several ways, the current or future editors of this journal can improve credibility of results published in this journal. First, results with weak evidence (p-values between .05 and .01) should only be reported as suggestive results that require replication or even request a replication before publication. Second, editors should try to reduce publication bias by prioritizing research questions over results. A well-conducted study with an important question should be published even if the results are not statistically significant. Pre-registration and registered reports can help to reduce publication bias. Editors may also ask for follow-up studies with higher power to follow up on a non-significant result.

Publication bias also implies that point estimates of effect sizes are inflated. It is therefore important to take uncertainty in this estimates into account. Small samples with large sampling error are usually unable to provide meaningful information about effect sizes and conclusions should be limited to the direct of an effect.

The present results serve as a benchmark for future years to track progress in this journal to ensure trust in research by evolutionary psychologists.

Replicability of Research in Frontiers of Psychology

Replicability, Replicability Audit, , , , , ,

Summary

The z-curve analysis of results in this journal shows (a) that many published results are based on studies with low to modest power, (b) selection for significance inflates effect size estimates and the discovery rate of reported results, and (c) there is no evidence that research practices have changed over the past decade. Readers should be careful when they interpret results and recognize that reported effect sizes are likely to overestimate real effect sizes, and that replication studies with the same sample size may fail to produce a significant result again. To avoid misleading inferences, I suggest using alpha = .005 as a criterion for valid rejections of the null-hypothesis. Using this criterion, the risk of a false positive result is below 2%. I also recommend computing a 99% confidence interval rather than the traditional 95% confidence interval for the interpretation of effect size estimates.

Given the low power of many studies, readers also need to avoid the fallacy to report non-significant results as evidence for the absence of an effect. With 50% power, the results can easily switch in a replication study so that a significant result becomes non-significant and a non-significant result becomes significant. However, selection for significance will make it more likely that significant results become non-significant than observing a change in the opposite direction.

The average power of studies in a heterogeneous journal like Frontiers of Psychology provides only circumstantial evidence for the evaluation of results. When other information is available (e.g., z-curve analysis of a discipline, author, or topic, it may be more appropriate to use this information).

Report

Frontiers of Psychology was created in 2010 as a new online-only journal for psychology. It covers many different areas of psychology, although some areas have specialized Frontiers journals like Frontiers in Behavioral Neuroscience.

The business model of Frontiers journals relies on publishing fees of authors, while published articles are freely available to readers.

The number of articles in Frontiers of Psychology has increased quickly from 131 articles in 2010 to 8,072 articles in 2022 (source Web of Science). With over 8,000 published articles Frontiers of Psychology is an important outlet for psychological researchers to publish their work. Many specialized, print-journals publish fewer than 100 articles a year. Thus, Frontiers of Psychology offers a broad and large sample of psychological research that is equivalent to a composite of 80 or more specialized journals.

Another advantage of Frontiers of Psychology is that it has a relatively low rejection rate compared to specialized journals that have limited journal space. While high rejection rates may allow journals to prioritize exceptionally good research, articles published in Frontiers of Psychology are more likely to reflect the common research practices of psychologists.

To examine the replicability of research published in Frontiers of Psychology, I downloaded all published articles as PDF files, converted PDF files to text files, and extracted test-statistics (F, t, and z-tests) from published articles. Although this method does not capture all published results, there is no a priori reason that results reported in this format differ from other results. More importantly, changes in research practices such as higher power due to larger samples would be reflected in all statistical tests.

As Frontiers of Psychology only started shortly before the replication crisis in psychology increased awareness about the problem of low statistical power and selection for significance (publication bias), I was not able to examine replicability before 2011. I also found little evidence of changes in the years from 2010 to 2015. Therefore, I use this time period as the starting point and benchmark for future years.

Figure 1 shows a z-curve plot of results published from 2010 to 2014. All test-statistics are converted into z-scores. Z-scores greater than 1.96 (the solid red line) are statistically significant at alpha = .05 (two-sided) and typically used to claim a discovery (rejection of the null-hypothesis). Sometimes even z-scores between 1.65 (the dotted red line) and 1.96 are used to reject the null-hypothesis either as a one-sided test or as marginal significance. Using alpha = .05, the plot shows 71% significant results, which is called the observed discovery rate (ODR).

Visual inspection of the plot shows a peak of the distribution right at the significance criterion. It also shows that z-scores drop sharply on the left side of the peak when the results do not reach the criterion for significance. This wonky distribution cannot be explained with sampling error. Rather it shows a selective bias to publish significant results by means of questionable practices such as not reporting failed replication studies or inflating effect sizes by means of statistical tricks. To quantify the amount of selection bias, z-curve fits a model to the distribution of significant results and estimates the distribution of non-significant (i.e., the grey curve in the range of non-significant results). The discrepancy between the observed distribution and the expected distribution shows the file-drawer of missing non-significant results. Z-curve estimates that the reported significant results are only 31% of the estimated distribution. This is called the expected discovery rate (EDR). Thus, there are more than twice as many significant results as the statistical power of studies justifies (71% vs. 31%). Confidence intervals around these estimates show that the discrepancy is not just due to chance, but active selection for significance.

Using a formula developed by Soric (1989), it is possible to estimate the false discovery risk (FDR). That is, the probability that a significant result was obtained without a real effect (a type-I error). The estimated FDR is 12%. This may not be alarming, but the risk varies as a function of the strength of evidence (the magnitude of the z-score). Z-scores that correspond to p-values close to p =.05 have a higher false positive risk and large z-scores have a smaller false positive risk. Moreover, even true results are unlikely to replicate when significance was obtained with inflated effect sizes. The most optimistic estimate of replicability is the expected replication rate (ERR) of 69%. This estimate, however, assumes that a study can be replicated exactly, including the same sample size. Actual replication rates are often lower than the ERR and tend to fall between the EDR and ERR. Thus, the predicted replication rate is around 50%. This is slightly higher than the replication rate in the Open Science Collaboration replication of 100 studies which was 37%.

Figure 2 examines how things have changed in the next five years.

The observed discovery rate decreased slightly, but statistically significantly, from 71% to 66%. This shows that researchers reported more non-significant results. The expected discovery rate increased from 31% to 40%, but the overlapping confidence intervals imply that this is not a statistically significant increase at the alpha = .01 level. (if two 95%CI do not overlap, the difference is significant at around alpha = .01). Although smaller, the difference between the ODR of 60% and the EDR of 40% is statistically significant and shows that selection for significance continues. The ERR estimate did not change, indicating that significant results are not obtained with more power. Overall, these results show only modest improvements, suggesting that most researchers who publish in Frontiers in Psychology continue to conduct research in the same way as they did before, despite ample discussions about the need for methodological reforms such as a priori power analysis and reporting of non-significant results.

The results for 2020 show that the increase in the EDR was a statistical fluke rather than a trend. The EDR returned to the level of 2010-2015 (29% vs. 31), but the ODR remained lower than in the beginning, showing slightly more reporting of non-significant results. The size of the file drawer remains large with an ODR of 66% and an EDR of 72%.

The EDR results for 2021 look again better, but the difference to 2020 is not statistically significant. Moreover, the results in 2022 show a lower EDR that matches the EDR in the beginning.

Overall, these results show that results published in Frontiers in Psychology are selected for significance. While the observed discovery rate is in the upper 60%s, the expected discovery rate is around 35%. Thus, the ODR is nearly twice the rate of the power of studies to produce these results. Most concerning is that a decade of meta-psychological discussions about research practices has not produced any notable changes in the amount of selection bias or the power of studies to produce replicable results.

How should readers of Frontiers in Psychology articles deal with this evidence that some published results were obtained with low power and inflated effect sizes that will not replicate? One solution is to retrospectively change the significance criterion. Comparisons of the evidence in original studies and replication outcomes suggest that studies with a p-value below .005 tend to replicate at a rate of 80%, whereas studies with just significant p-values (.050 to .005) replicate at a much lower rate (Schimmack, 2022). Demanding stronger evidence also reduces the false positive risk. This is illustrated in the last figure that uses results from all years, given the lack of any time trend.

In the Figure the red solid line moved to z = 2.8; the value that corresponds to p = .005, two-sided. Using this more stringent criterion for significance, only 45% of the z-scores are significant. Another 25% were significant with alpha = .05, but are no longer significant with alpha = .005. As power decreases when alpha is set to more stringent, lower, levels, the EDR is also reduced to only 21%. Thus, there is still selection for significance. However, the more effective significance filter also selects for more studies with high power and the ERR remains at 72%, even with alpha = .005 for the replication study. If the replication study used the traditional alpha level of .05, the ERR would be even higher, which explains the finding that the actual replication rate for studies with p < .005 is about 80%.

The lower alpha also reduces the risk of false positive results, even though the EDR is reduced. The FDR is only 2%. Thus, the null-hypothesis is unlikely to be true. The caveat is that the standard null-hypothesis in psychology is the nil-hypothesis and that the population effect size might be too small to be of practical significance. Thus, readers who interpret results with p-values below .005 should also evaluate the confidence interval around the reported effect size, using the more conservative 99% confidence interval that correspondence to alpha = .005 rather than the traditional 95% confidence interval. In many cases, this confidence interval is likely to be wide and provide insufficient information about the strength of an effect.

Predicting Replication Outcomes: Prediction Markets vs. R-Index

Replicability, , ,

Conclusion

Gordon et al. (2021) conducted a meta-analysis of 103 studies that were included in prediction markets to forecast the outcome of replication studies. The results show that prediction markets can forecast replication outcomes above chance levels, but the value of this information is limited. Without actual replication studies, it remains unclear which published results can be trusted or not. Here I compare the performance of prediction markets to the R-Index and the closely related p < .005 rule. These statistical forecasts perform nearly as well as markets and are much easier to use to make sense of thousands of published articles. However, even these methods have a high failure rate. The best solution to this problem is to rely on meta-analyses of studies rather than to predict the outcome of a single study. In addition to meta-analyses, it will be necessary to conduct new studies that are conducted with high scientific integrity to provide solid empirical foundations for psychology. Claims that are not supported by bias-corrected meta-analyses or new preregistered studies are merely suggestive and currently lack empirical support.

Introduction

Since 2011, it became apparent that many published results in psychology, especially social psychology fail to replicate in direct replication studies (Open Science Collaboration, 2015). In social psychology the success rate of replication studies is so low (25%) that it makes sense to bet on replication failures. This would produce 75% successful outcomes, but it would also imply that an entire literature has to be discarded.

It is practically impossible to redo all of the published studies to assess their replicability. Thus, several projects have attempted to predict replication outcomes of individual studies. One strategy is to conduct prediction markets in which participants can earn real money by betting on replication outcomes. There have been four prediction markets with a total of 103 studies with known replication outcomes (Gordon et al., 2021). The key findings are summarized in Table 1.

Markets have a good overall success rate, (28+47)/103 = 73% that is above chance (flipping a coin). Prediction markets are better at predicting failures, 28/31 = 90%, than predicting successes, 47/72 = 65%. The modest success rate for success is a problem because it would be more valuable to be able to identify studies that will replicate and do not require a new study to verify the results.

Another strategy to predict replication outcomes relies on the fact that the p-values of original studies and the p-values of replication studies are influenced by the statistical power of a study (Brunner & Schimmack, 2020). Studies with higher power are more likely to produce lower p-values and more likely to produce significant p-values in replication studies. As a result, p-values also contain valuable information about replication outcomes. Gordon et al. (2021) used p < .005 as a rule to predict replication outcomes. Table 2 shows the performance of this simple rule.

The overall success rate of this rule is nearly as good as the prediction markets, (39+35)/103 = 72%; a difference by k = 1 studies. The rule does not predict failures as well as the markets, 39/54 = 72% (vs. 90%), but it predicts successes slightly better than the markets, 35/49 = 71% (vs. 65%).

A logistic regression analysis showed that both predictors independently contribute to the prediction of replication outcomes, market b = 2.50, se = .68, p = .0002; p < .005 rule: b = 1.44, se = .48, p = .003.

In short, p-values provide valuable information about the outcome of replication studies.

The R-Index

Although a correlation between p-values and replication outcomes follows logically from the influence of power on p-values in original and replication studies, the cut-off value of .005 appears to be arbitrary. Gordon et al. (2017) justify its choice with an article by Benjamin et al. (2017) that recommended a lower significance level (alpha) to ensure a lower false positive risk. Moreover, they advocated for this rule for new studies that preregister hypotheses and do not suffer from selection bias. In contrast, the replication crisis was caused by selection for significance which produced success rates of 90% or more in psychology journals (Motyl et al., 2017; Sterling, 1959; Sterling et al., 1995). One main reason for replication failures is that selection for significance inflates effect sizes and due to regression to the mean, effect sizes in replication studies are bound to be weaker, resulting in non-significant results, especially if the original p-value was close to the threshold value of alpha = .05. The Open Science Collaboration (2015) replicability project showed that effect sizes are on average inflated by over 100%.

The R-Index provides a theoretical rational for the choice of a cut-off value for p-values. The theoretical cutoff value happens to be p = .0084. The fact that it is close to Benjamin et al.’s (2017) value of .005 is merely a coincidence.

P-values can be transformed into estimates of the statistical power of a study. These estimates rely on the observed effect size of a study and are sometimes called observed power or post-hoc power because power is computed after the results of a study are known. Figure 1 illustrates observed power with an example of a z-test that produced a z-statistic of 2.8 which corresponds to a two-sided p-value of .005.

A p-value of .005 corresponds to z-value of 2.8 for the standard normal distribution centered over zero (the nil-hypothesis). The standard level of statistical significance, alpha = .05 (two-sided) corresponds to z-value of 1.96. Figure 1 shows the sampling distribution of studies with a non-central z-score of 2.8. The green line cuts this distribution into a smaller area of 20% below the significance level and a larger area of 80% above the significance level. Thus, the observed power is 80%.

Selection for significance implies truncating the normal distribution at the level of significance. This means the 20% of non-significant results are discarded. As a result, the median of the truncated distribution is higher than the median of the full normal distribution. The new median can be found using the truncnorm package in R.

qtruncnorm(.5,a = qnorm(1-.05/2),mean=2.8) = 3.05

This value corresponds to an observed power of

qnorm(3.05,qnorm(1-.05/2) = .86

Thus, selection for significance inflates observed power of 80% to 86%. The amount of inflation is larger when power is lower. With 20% power, the inflated power after selection for significance is 67%.

Figure 3 shows the relationship between inflated power on the x-axis and adjusted power on the y-axis. The blue curve uses the truncnorm package. The green line shows the simplified R-Index that simply substracts the amount of inflation from the inflated power. For example, if inflated power is 86%, the inflation is 1-.86 = 14% and subtracting the inflation gives an R-Index of 86-14 = 82%. This is close to the actual value of 80% that produced the inflated value of 86%.

Figure 4 shows that the R-Index is conservative (underestimates power) when power is over 50%, but is liberal (overestimates power) when power is below 50%. The two methods are identical when power is 50% and inflated power is 75%. This is a fortunate co-incidence because studies with more than 50% power are expected to replicate and studies with less than 50% power are expected to fail in a replication attempt. Thus, the simple R-Index makes the same dichotomous predictions about replication outcomes as the more sophisticated approach to find the median of the truncated normal distribution.

The inflated power for actual power of 50% is 75% and 75% power corresponds to a z-score of 2.63, which in turn corresponds to a p-value of p = .0084.

Performance of the R-Index is slightly worse than the p < .005 rule because the R-Index predicts 5 more successes, but 4 of these predictions are failures. Given the small sample size, it is not clear whether this difference is reliable.

In sum, the R-Index is based on a transformation of p-values into estimates of statistical power, while taking into account that observed power is inflated when studies are selected for significance. It provides a theoretical rational for the atheoretical p < .005 rule, because this rule roughly cuts p-values into p-values with more or less than 50% power.

Predicting Success Rates

The overall success rate across the 103 replication studies was 50/103 = 49%. This percentage cannot be generalized to a specific population of studies because the 103 are not a representative sample of studies. Only the Open Science Collaboration project used somewhat representative sampling. However, the 49% success rate can be compared to the success rates of different prediction methods. For example, prediction markets predict a success rate of 72/103 = 70%, a significant difference (Gordon et al., 2021). In contrast, the R-Index predicts a success rate of 54/103 = 52%, which is closer to the actual success rate. The p < .005 rule does even better with a predicted success rate of 49/103 = 48%.

Another method that has been developed to estimate the expected replication rate is z-curve (Bartos & Schimmack, 2021; Brunner & Schimmack, 2020). Z-curve transforms p-values into z-scores and then fits a finite mixture model to the distribution of significant p-values. Figure 5 illustrates z-curve with the p-values from the 103 replicated studies.

The z-curve estimate of the expected replication rate is 60%. This is better than the prediction market, but worse than the R-Index or the p < .005 rule. However, the 95%CI around the ERR includes the true value of 49%. Thus, sampling error alone might explain this discrepancy. However, Bartos and Schimmack (2021) discussed several other reasons why the ERR may overestimate the success rate of actual replication studies. One reason is that actual replication studies are not perfect replicas of the original studies. So called, hidden moderators may create differences between original and replication studies. In this case, selection for significance produces even more inflation that the model assumes. In the worst case scenario, a better estimate of actual replication outcomes might be the expected discovery rate (EDR), which is the power of all studies that were conducted, including non-significant studies. The EDR for the 103 studies is 28%, but the 95%CI is wide and includes the actual rate of 49%. Thus, the dataset is too small to decide between the ERR or the EDR as best estimates of actual replication outcomes. At present it is best to consider the EDR the worst possible and the ERR the best possible scenario and to expect the actual replication rate to fall within this interval.

Social Psychology

The 103 studies cover studies from experimental economics, cognitive psychology, and social psychology. Social psychology has the largest set of studies (k = 54) and the lowest success rate, 33%. The prediction markets overpredict successes, 50%. The R-Index also overpredicted successes, 46%. The p < .005 rule had the least amount of bias, 41%.

Z-curve predicted an ERR of 55% s and the actual success rate fell outside the 95% confidence interval, 34% to 74%. The EDR of 22% underestimates the success rate, but the 95%CI is wide and includes the true value, 95%CI = 5% to 70%. Once more the actual success rate is between the EDR and the ERR estimates, 22% < 34% < 55%.

In short, prediction models appear to overpredict replication outcomes in social psychology. One reason for this might be that hidden moderators make it difficult to replicate studies in social psychology which adds additional uncertainty to the outcome of replication studies.

Regarding predictions of individual studies, prediction markets achieved an overall success rate of 76%. Prediction markets were good at predicting failures, 25/27 = 93%, but not so good in predicting successes, 16/27 = 59%.

The R-Index performed as well as the prediction markets with one more prediction of a replication failure.

The p < .005 rule was the best predictor because it predicted more replication failures.

Performance could be increased by combining prediction markets and the R-Index and only bet on successes when both predictors predicted a success. In particular, the prediction of success improved to 14/19 = 74%. However, due to the small sample size it is not clear whether this is a reliable finding.

Non-Social Studies

The remaining k = 56 studies had a higher success rate, 65%. The prediction markets overpredicted success, 92%. The R-Index underpredicted successes, 59%. The p < .005 rule underpredicted successes even more.

This time z-curve made the best prediction with an ERR of 67%, 95%CI = 45% to 86%. The EDR underestimates the replication rate, although the 95%CI is very wide and includes the actual success rate, 5% to 81%. The fact that z-curve overestimated replicability for social psychology, but not for other areas, suggests that hidden moderators may contribute to the replication problems in social psychology.

For predictions of individual outcomes, prediction markets had a success rate of (3 + 31)/49 = 76%. The good performance is due to the high success rate. Simply betting on success would have produced 32/49 = 65% successes. Predictions of failures had a s success rate of 3/4 = 75% and predictions of successes had a success rate of 31/45 = 69%.

The R-Index had a lower success rate of (9 +21)/49 = 61%. The R-Index was particularly poor at predicting failures, 9/20 = 45%, but was slightly better at predicting successes than the prediction markets, 21/29 = 72%.

The p < .500 rule had a success rate equal to the R-Index, (10 + 20)/49 = 61%, with one more correctly predicted failure and one less correctly predicted success.

Discussion

The present results reproduce the key findings of Gordon et al. (2021). First, prediction markets overestimate the success of actual replication studies. Second, prediction markets have some predictive validity in forecasting the outcome of individual replication studies. Third, a simple rule based on p-values also can forecast replication outcomes.

The present results also extend Gordon et al.’s (2021) findings based on additional analyses. First, I compared the performance of prediction markets to z-curve as a method for the prediction of the success rates of replication outcomes (Bartos & Schimmack, 2021; Brunner & Schimmack, 2021). Z-curve overpredicted success rates for all studies and for social psychology, but was very accurate for the remaining studies (economics, cognition). In all three comparisons, z-curve performed better than prediction markets. Z-curve also has several additional advantages over prediction markets. First, it is much easier to code a large set of test statistics than to run prediction markets. As a result, z-curve has already been used to estimate the replication rates for social psychology based on thousands of test statistics, whereas estimates of prediction markets are based on just over 50 studies. Second, z-curve is based on sound statistical principles that link the outcomes of original studies to the outcomes of replication studies (Brunner & Schimmack, 2020). In contrast, prediction markets rest on unknown knowledge of market participants that can vary across markets. Third, z-curve estimates are provided with validated information about the uncertainty in the estimates, whereas prediction markets provide no information about uncertainty and uncertainty is large because markets tend to be small. In conclusion, z-curve is more efficient and provides better estimates of replication rates than prediction markets.

The main goal of prediction markets is to assess the credibility of individual studies. Ideally, prediction markets would help consumers of published research to distinguish between studies that produced real findings (true positives) and studies that produced false findings (false positives) without the need to run additional studies. The encouraging finding is that prediction markets have some predictive validity and can distinguish between studies that replicate and studies that do not replicate. However, to be practically useful it is necessary to assess the practical usefulness of the information that is provided by prediction markets. Here we need to distinguish the practical consequences of replication failures and successes. Within the statistical framework of nil-hypothesis significance testing, successes and failures have different consequences.

A replication failure increases uncertainty about the original finding. Thus, more research is needed to understand why the results diverged. This is also true for market predictions. Predictions that a study would fail to replicate cast doubt about the original study, but do not provide conclusive evidence that the original study reported a false positive result. Thus, further studies are needed, even if a market predicts a failure. In contrast, successes are more informative. Replicating a previous finding successfully strengthens the original findings and provides fairly strong evidence that a finding was not a false positive result. Unfortunately, the mere prediction that a finding will replicate does not provide the same reassurance because markets only have an accuracy of about 70% when they predict a successful replication. The p < .500 rule is much easier to implement, but its ability to forecast successes is also around 70%. Thus, neither markets nor a simple statistical rule are accurate enough to avoid actual replication studies.

Meta-Analysis

The main problem of prediction markets and other forecasting projects is that single studies are rarely enough to provide evidence that is strong enough to evaluate theoretical claims. It is therefore not particularly important whether one study can be replicated successfully or not, especially when direct replications are difficult or impossible. For this reason, psychologists have relied for a long time on meta-analyses of similar studies to evaluate theoretical claims.

It is surprising that prediction markets have forecasted the outcome of studies that have been replicated many times before the outcome of a new replication study was predicted. Take the replication of Schwarz, Strack, and Mai (1991) in Many Labs 2 as an example. This study manipulated the item-order of questions about marital satisfaction and life-satisfaction and suggested that a question about marital satisfaction can prime information that is used in life-satisfaction judgments. Schimmack and Oishi (2005) conducted a meta-analysis of the literature and showed that the results by Schwarz et al. (1991) were unusual and that the actual effect size is much smaller. Apparently, the market participants were unaware of this meta-analysis and predicted that the original result would replicate successfully (probability of success = 72%). Contrary to the market, the study failed to replicate. This example suggests that meta-analyses might be more valuable than prediction markets or the p-value of a single study.

The main obstacle for the use of meta-analyses is that many published meta-analyses fail to take selection for significance into account and overestimate replicability. However, new statistical methods that correct for selection bias may address this problem. The R-Index is a rather simple tool that allows to correct for selection bias in small sets of studies. I use the article by Nairne et al. (2008) that was used for the OSC project as an example. The replication project focused on Study 2 that produced a p-value of .026. Based on this weak evidence alone, the R-Index would predict a replication failure (observed power = .61, inflation = .39, R-Index = .61 – .39 = .22). However, Study 1 produced much more convincing evidence for the effect, p = .0007. If this study had been picked for the replication attempt, the R-Index would have predicted a successful outcome (observed power = .92, inflation = .08, R-Index = .84). A meta-analysis would average across the two power estimates and also predict a successful replication outcome (mean observed power = .77, inflation = .23, R-Index = .53). The actual replication study was significant with p = .007 (observed power = .77, inflation = .23, R-Index = .53). A meta-analysis across all three studies also suggests that the next study will be a successful replication (R-Index = .53), but the R-Index also shows that replication failures are likely because the studies have relatively low power. In short, prediction markets may be useful when only a single study is available, but meta-analysis are likely to be superior predictors of replication outcomes when prior replication studies are available.

Conclusion

Gordon et al. (2021) conducted a meta-analysis of 103 studies that were included in prediction markets to forecast the outcome of replication studies. The results show that prediction markets can forecast replication outcomes above chance levels, but the value of this information is limited. Without actual replication studies, it remains unclear which published results can be trusted or not. Statistical methods that simply focus on the strength of evidence in original studies perform nearly as well and are much easier to use to make sense of thousands of published articles. However, even these methods have a high failure rate. The best solution to this problem is to rely on meta-analyses of studies rather than to predict the outcome of a single study. In addition to meta-analyses, it will be necessary to conduct new studies that are conducted with high scientific integrity to provide solid empirical foundations for psychology.

Replicability Rankings 2010-2020

Power, Replicability, Replicability Ranking, Statistical Power, Z-Curve

Welcome to the replicability rankings for 120 psychology journals. More information about the statistical method that is used to create the replicability rankings can be found elsewhere (Z-Curve; Video Tutorial; Talk; Examples). The rankings are based on automated extraction of test statistics from all articles published in these 120 journals from 2010 to 2020 (data). The results can be reproduced with the R-package zcurve.

To give a brief explanation of the method, I use the journal with the highest ranking and the journal with the lowest ranking as examples. Figure 1 shows the z-curve plot for the 2nd highest ranking journal for the year 2020 (the Journal of Organizational Psychology is ranked #1, but it has very few test statistics). Plots for all journals that include additional information and information about test statistics are available by clicking on the journal name. Plots for previous years can be found on the site for the 2010-2019 rankings (previous rankings).

To create the z-curve plot in Figure 1, the 361 test statistics were first transformed into exact p-values that were then transformed into absolute z-scores. Thus, each value represents the deviation from zero for a standard normal distribution. A value of 1.96 (solid red line) corresponds to the standard criterion for significance, p = .05 (two-tailed). The dashed line represents the treshold for marginal significance, p = .10 (two-tailed). A z-curve analysis fits a finite mixture model to the distribution of the significant z-scores (the blue density distribution on the right side of the solid red line). The distribution provides information about the average power of studies that produced a significant result. As power determines the success rate in future studies, power after selection for significance is used to estimate replicability. For the present data, the z-curve estimate of the replication rate is 84%. The bootstrapped 95% confidence interval around this estimate ranges from 75% to 92%. Thus, we would expect the majority of these significant results to replicate.

However, the graph also shows some evidence that questionable research practices produce too many significant results. The observed discovery rate (i.e., the percentage of p-values below .05) is 82%. This is outside of the 95%CI of the estimated discovery rate which is represented by the grey line in the range of non-significant results; EDR = .31%, 95%CI = 18% to 81%. We see that there are fewer results reported than z-curve predicts. This finding casts doubt about the replicability of the just significant p-values. The replicability rankings ignore this problem, which means that the predicted success rates are overly optimistic. A more pessimistic predictor of the actual success rate is the EDR. However, the ERR still provides useful information to compare power of studies across journals and over time.

Figure 2 shows a journal with a low ERR in 2020.

The estimated replication rate is 64%, with a 95%CI ranging from 55% to 73%. The 95%CI does not overlap with the 95%CI for the Journal of Sex Research, indicating that this is a significant difference in replicability. Visual inspection also shows clear evidence for the use of questionable research practices with a lot more results that are just significant than results that are not significant. The observed discovery rate of 75% is inflated and outside the 95%CI of the EDR that ranges from 10% to 56%.

To examine time trends, I regressed the ERR of each year on the year and computed the predicted values and 95%CI. Figure 3 shows the results for the journal Social Psychological and Personality Science as an example (x = 0 is 2010, x = 1 is 2020). The upper bound of the 95%CI for 2010, 62%, is lower than the lower bound of the 95%CI for 2020, 74%.

This shows a significant difference with alpha = .01. I use alpha = .01 so that only 1.2 out of the 120 journals are expected to show a significant change in either direction by chance alone. There are 22 journals with a significant increase in the ERR and no journals with a significant decrease. This shows that about 20% of these journals have responded to the crisis of confidence by publishing studies with higher power that are more likely to replicate.

Rank  JournalObserved 2020Predicted 2020Predicted 2010
1Journal of Organizational Psychology88 [69 ; 99]84 [75 ; 93]73 [64 ; 81]
2Journal of Sex Research84 [75 ; 92]84 [74 ; 93]75 [65 ; 84]
3Evolution & Human Behavior84 [74 ; 93]83 [77 ; 90]62 [56 ; 68]
4Judgment and Decision Making81 [74 ; 88]83 [77 ; 89]68 [62 ; 75]
5Personality and Individual Differences81 [76 ; 86]81 [78 ; 83]68 [65 ; 71]
6Addictive Behaviors82 [75 ; 89]81 [77 ; 86]71 [67 ; 75]
7Depression & Anxiety84 [76 ; 91]81 [77 ; 85]67 [63 ; 71]
8Cognitive Psychology83 [75 ; 90]81 [76 ; 87]71 [65 ; 76]
9Social Psychological and Personality Science85 [78 ; 92]81 [74 ; 89]54 [46 ; 62]
10Journal of Experimental Psychology – General80 [75 ; 85]80 [79 ; 81]67 [66 ; 69]
11J. of Exp. Psychology – Learning, Memory & Cognition81 [75 ; 87]80 [77 ; 84]73 [70 ; 77]
12Journal of Memory and Language79 [73 ; 86]80 [76 ; 83]73 [69 ; 77]
13Cognitive Development81 [75 ; 88]80 [75 ; 85]67 [62 ; 72]
14Sex Roles81 [74 ; 88]80 [75 ; 85]72 [67 ; 77]
15Developmental Psychology74 [67 ; 81]80 [75 ; 84]67 [63 ; 72]
16Canadian Journal of Experimental Psychology77 [65 ; 90]80 [73 ; 86]74 [68 ; 81]
17Journal of Nonverbal Behavior73 [59 ; 84]80 [68 ; 91]65 [53 ; 77]
18Memory and Cognition81 [73 ; 87]79 [77 ; 81]75 [73 ; 77]
19Cognition79 [74 ; 84]79 [76 ; 82]70 [68 ; 73]
20Psychology and Aging81 [74 ; 87]79 [75 ; 84]74 [69 ; 79]
21Journal of Cross-Cultural Psychology83 [76 ; 91]79 [75 ; 83]75 [71 ; 79]
22Psychonomic Bulletin and Review79 [72 ; 86]79 [75 ; 83]71 [67 ; 75]
23Journal of Experimental Social Psychology78 [73 ; 84]79 [75 ; 82]52 [48 ; 55]
24JPSP-Attitudes & Social Cognition82 [75 ; 88]79 [69 ; 89]55 [45 ; 65]
25European Journal of Developmental Psychology75 [64 ; 86]79 [68 ; 91]74 [62 ; 85]
26Journal of Business and Psychology82 [71 ; 91]79 [68 ; 90]74 [63 ; 85]
27Psychology of Religion and Spirituality79 [71 ; 88]79 [66 ; 92]72 [59 ; 85]
28J. of Exp. Psychology – Human Perception and Performance79 [73 ; 84]78 [77 ; 80]75 [73 ; 77]
29Attention, Perception and Psychophysics77 [72 ; 82]78 [75 ; 82]73 [70 ; 76]
30Psychophysiology79 [74 ; 84]78 [75 ; 82]66 [62 ; 70]
31Psychological Science77 [72 ; 84]78 [75 ; 82]57 [54 ; 61]
32Quarterly Journal of Experimental Psychology81 [75 ; 86]78 [75 ; 81]72 [69 ; 74]
33Journal of Child and Family Studies80 [73 ; 87]78 [74 ; 82]67 [63 ; 70]
34JPSP-Interpersonal Relationships and Group Processes81 [74 ; 88]78 [73 ; 82]53 [49 ; 58]
35Journal of Behavioral Decision Making77 [70 ; 86]78 [72 ; 84]66 [60 ; 72]
36Appetite78 [73 ; 84]78 [72 ; 83]72 [67 ; 78]
37Journal of Comparative Psychology79 [65 ; 91]78 [71 ; 85]68 [61 ; 75]
38Journal of Religion and Health77 [57 ; 94]78 [70 ; 87]75 [67 ; 84]
39Aggressive Behaviours82 [74 ; 90]78 [70 ; 86]70 [62 ; 78]
40Journal of Health Psychology74 [64 ; 82]78 [70 ; 86]72 [64 ; 80]
41Journal of Social Psychology78 [70 ; 87]78 [70 ; 86]69 [60 ; 77]
42Law and Human Behavior81 [71 ; 90]78 [69 ; 87]70 [61 ; 78]
43Psychological Medicine76 [68 ; 85]78 [66 ; 89]74 [63 ; 86]
44Political Psychology73 [59 ; 85]78 [65 ; 92]59 [46 ; 73]
45Acta Psychologica81 [75 ; 88]77 [74 ; 81]73 [70 ; 76]
46Experimental Psychology73 [62 ; 83]77 [73 ; 82]73 [68 ; 77]
47Archives of Sexual Behavior77 [69 ; 83]77 [73 ; 81]78 [74 ; 82]
48British Journal of Psychology73 [65 ; 81]77 [72 ; 82]74 [68 ; 79]
49Journal of Cognitive Psychology77 [69 ; 84]77 [72 ; 82]74 [69 ; 78]
50Journal of Experimental Psychology – Applied82 [75 ; 88]77 [72 ; 82]70 [65 ; 76]
51Asian Journal of Social Psychology79 [66 ; 89]77 [70 ; 84]70 [63 ; 77]
52Journal of Youth and Adolescence80 [71 ; 89]77 [70 ; 84]72 [66 ; 79]
53Memory77 [71 ; 84]77 [70 ; 83]71 [65 ; 77]
54European Journal of Social Psychology82 [75 ; 89]77 [69 ; 84]61 [53 ; 69]
55Social Psychology81 [73 ; 90]77 [67 ; 86]73 [63 ; 82]
56Perception82 [74 ; 88]76 [72 ; 81]78 [74 ; 83]
57Journal of Anxiety Disorders80 [71 ; 89]76 [72 ; 80]71 [67 ; 75]
58Personal Relationships65 [54 ; 76]76 [68 ; 84]62 [54 ; 70]
59Evolutionary Psychology63 [51 ; 75]76 [67 ; 85]77 [68 ; 86]
60Journal of Research in Personality63 [46 ; 77]76 [67 ; 84]70 [61 ; 79]
61Cognitive Behaviour Therapy88 [73 ; 99]76 [66 ; 86]68 [58 ; 79]
62Emotion79 [73 ; 85]75 [72 ; 79]67 [64 ; 71]
63Animal Behavior79 [72 ; 87]75 [71 ; 80]68 [64 ; 73]
64Group Processes & Intergroup Relations80 [73 ; 87]75 [71 ; 80]60 [56 ; 65]
65JPSP-Personality Processes and Individual Differences78 [70 ; 86]75 [70 ; 79]64 [59 ; 69]
66Psychology of Men and Masculinity88 [77 ; 96]75 [64 ; 87]78 [67 ; 89]
67Consciousness and Cognition74 [67 ; 80]74 [69 ; 80]67 [62 ; 73]
68Personality and Social Psychology Bulletin78 [72 ; 84]74 [69 ; 79]57 [52 ; 62]
69Journal of Cognition and Development70 [60 ; 80]74 [67 ; 81]65 [59 ; 72]
70Journal of Applied Psychology69 [59 ; 78]74 [67 ; 80]73 [66 ; 79]
71European Journal of Personality80 [67 ; 92]74 [65 ; 83]70 [61 ; 79]
72Journal of Positive Psychology75 [65 ; 86]74 [65 ; 83]66 [57 ; 75]
73Journal of Research on Adolescence83 [74 ; 92]74 [62 ; 87]67 [55 ; 79]
74Psychopharmacology75 [69 ; 80]73 [71 ; 75]67 [65 ; 69]
75Frontiers in Psychology75 [70 ; 79]73 [70 ; 76]72 [69 ; 75]
76Cognitive Therapy and Research73 [66 ; 81]73 [68 ; 79]67 [62 ; 73]
77Behaviour Research and Therapy70 [63 ; 77]73 [67 ; 79]70 [64 ; 76]
78Journal of Educational Psychology82 [73 ; 89]73 [67 ; 79]76 [70 ; 82]
79British Journal of Social Psychology74 [65 ; 83]73 [66 ; 81]61 [54 ; 69]
80Organizational Behavior and Human Decision Processes70 [65 ; 77]72 [69 ; 75]67 [63 ; 70]
81Cognition and Emotion75 [68 ; 81]72 [68 ; 76]72 [68 ; 76]
82Journal of Affective Disorders75 [69 ; 83]72 [68 ; 76]74 [71 ; 78]
83Behavioural Brain Research76 [71 ; 80]72 [67 ; 76]70 [66 ; 74]
84Child Development81 [75 ; 88]72 [66 ; 78]68 [62 ; 74]
85Journal of Abnormal Psychology71 [60 ; 82]72 [66 ; 77]65 [60 ; 71]
86Journal of Vocational Behavior70 [59 ; 82]72 [65 ; 79]84 [77 ; 91]
87Journal of Experimental Child Psychology72 [66 ; 78]71 [69 ; 74]72 [69 ; 75]
88Journal of Consulting and Clinical Psychology81 [73 ; 88]71 [64 ; 78]62 [55 ; 69]
89Psychology of Music78 [67 ; 86]71 [64 ; 78]79 [72 ; 86]
90Behavior Therapy78 [69 ; 86]71 [63 ; 78]70 [63 ; 78]
91Journal of Occupational and Organizational Psychology66 [51 ; 79]71 [62 ; 80]87 [79 ; 96]
92Journal of Happiness Studies75 [65 ; 83]71 [61 ; 81]79 [70 ; 89]
93Journal of Occupational Health Psychology77 [65 ; 90]71 [58 ; 83]65 [52 ; 77]
94Journal of Individual Differences77 [62 ; 92]71 [51 ; 90]74 [55 ; 94]
95Frontiers in Behavioral Neuroscience70 [63 ; 76]70 [66 ; 75]66 [62 ; 71]
96Journal of Applied Social Psychology76 [67 ; 84]70 [63 ; 76]70 [64 ; 77]
97British Journal of Developmental Psychology72 [62 ; 81]70 [62 ; 79]76 [67 ; 85]
98Journal of Social and Personal Relationships73 [63 ; 81]70 [60 ; 79]69 [60 ; 79]
99Behavioral Neuroscience65 [57 ; 73]69 [64 ; 75]69 [63 ; 75]
100Psychology and Marketing71 [64 ; 77]69 [64 ; 74]67 [63 ; 72]
101Journal of Family Psychology71 [59 ; 81]69 [63 ; 75]62 [56 ; 68]
102Journal of Personality71 [57 ; 85]69 [62 ; 77]64 [57 ; 72]
103Journal of Consumer Behaviour70 [60 ; 81]69 [59 ; 79]73 [63 ; 83]
104Motivation and Emotion78 [70 ; 86]69 [59 ; 78]66 [57 ; 76]
105Developmental Science67 [60 ; 74]68 [65 ; 71]65 [63 ; 68]
106International Journal of Psychophysiology67 [61 ; 73]68 [64 ; 73]64 [60 ; 69]
107Self and Identity80 [72 ; 87]68 [60 ; 76]70 [62 ; 78]
108Journal of Counseling Psychology57 [41 ; 71]68 [55 ; 81]79 [66 ; 92]
109Health Psychology63 [50 ; 73]67 [62 ; 72]67 [61 ; 72]
110Hormones and Behavior67 [58 ; 73]66 [63 ; 70]66 [62 ; 70]
111Frontiers in Human Neuroscience68 [62 ; 75]66 [62 ; 70]76 [72 ; 80]
112Annals of Behavioral Medicine63 [53 ; 75]66 [60 ; 71]71 [65 ; 76]
113Journal of Child Psychology and Psychiatry and Allied Disciplines58 [45 ; 69]66 [55 ; 76]63 [53 ; 73]
114Infancy77 [69 ; 85]65 [56 ; 73]58 [50 ; 67]
115Biological Psychology64 [58 ; 70]64 [61 ; 67]66 [63 ; 69]
116Social Development63 [54 ; 73]64 [56 ; 72]74 [66 ; 82]
117Developmental Psychobiology62 [53 ; 70]63 [58 ; 68]67 [62 ; 72]
118Journal of Consumer Research59 [53 ; 67]63 [55 ; 71]58 [50 ; 66]
119Psychoneuroendocrinology63 [53 ; 72]62 [58 ; 66]61 [57 ; 65]
120Journal of Consumer Psychology64 [55 ; 73]62 [57 ; 67]60 [55 ; 65]

Personalized P-Values for Social/Personality Psychologists

Alpha Wars, False Discovery Rate, Replicability, Replicability Ranking, Science-Wise False Discovery Rate, Social Psychology

Last update 8/25/2021
(expanded to 410 social/personality psychologists; included Dan Ariely)

Introduction

Since Fisher invented null-hypothesis significance testing, researchers have used p < .05 as a statistical criterion to interpret results as discoveries worthwhile of discussion (i.e., the null-hypothesis is false). Once published, these results are often treated as real findings even though alpha does not control the risk of false discoveries.

Statisticians have warned against the exclusive reliance on p < .05, but nearly 100 years after Fisher popularized this approach, it is still the most common way to interpret data. The main reason is that many attempts to improve on this practice have failed. The main problem is that a single statistical result is difficult to interpret. However, when individual results are interpreted in the context of other results, they become more informative. Based on the distribution of p-values it is possible to estimate the maximum false discovery rate (Bartos & Schimmack, 2020; Jager & Leek, 2014). This approach can be applied to the p-values published by individual authors to adjust p-values to keep the risk of false discoveries at a reasonable level, FDR < .05.

Researchers who mainly test true hypotheses with high power have a high discovery rate (many p-values below .05) and a low false discovery rate (FDR < .05). Figure 1 shows an example of a researcher who followed this strategy (for a detailed description of z-curve plots, see Schimmack, 2021).

We see that out of the 317 test-statistics retrieved from his articles, 246 were significant with alpha = .05. This is an observed discovery rate of 78%. We also see that this discovery rate closely matches the estimated discovery rate based on the distribution of the significant p-values, p < .05. The EDR is 79%. With an EDR of 79%, the maximum false discovery rate is only 1%. However, the 95%CI is wide and the lower bound of the CI for the EDR, 27%, allows for 14% false discoveries.

When the ODR matches the EDR, there is no evidence of publication bias. In this case, we can improve the estimates by fitting all p-values, including the non-significant ones. With a tighter CI for the EDR, we see that the 95%CI for the maximum FDR ranges from 1% to 3%. Thus, we can be confident that no more than 5% of the significant results wit alpha = .05 are false discoveries. Readers can therefore continue to use alpha = .05 to look for interesting discoveries in Matsumoto’s articles.

Figure 3 shows the results for a different type of researcher who took a risk and studied weak effect sizes with small samples. This produces many non-significant results that are often not published. The selection for significance inflates the observed discovery rate, but the z-curve plot and the comparison with the EDR shows the influence of publication bias. Here the ODR is similar to Figure 1, but the EDR is only 11%. An EDR of 11% translates into a large maximum false discovery rate of 41%. In addition, the 95%CI of the EDR includes 5%, which means the risk of false positives could be as high as 100%. In this case, using alpha = .05 to interpret results as discoveries is very risky. Clearly, p < .05 means something very different when reading an article by David Matsumoto or Shelly Chaiken.

Rather than dismissing all of Chaiken’s results, we can try to lower alpha to reduce the false discovery rate. If we set alpha = .01, the FDR is 15%. If we set alpha = .005, the FDR is 8%. To get the FDR below 5%, we need to set alpha to .001.

A uniform criterion of FDR < 5% is applied to all researchers in the rankings below. For some this means no adjustment to the traditional criterion. For others, alpha is lowered to .01, and for a few even lower than that.

The rankings below are based on automatrically extracted test-statistics from 40 journals (List of journals). The results should be interpreted with caution and treated as preliminary. They depend on the specific set of journals that were searched, the way results are being reported, and many other factors. The data are available (data.drop) and researchers can exclude articles or add articles and run their own analyses using the z-curve package in R (https://replicationindex.com/2020/01/10/z-curve-2-0/).

I am also happy to receive feedback about coding errors. I also recommended to hand-code articles to adjust alpha for focal hypothesis tests. This typically lowers the EDR and increases the FDR. For example, the automated method produced an EDR of 31 for Bargh, whereas hand-coding of focal tests produced an EDR of 12 (Bargh-Audit).

And here are the rankings. The results are fully automated and I was not able to cover up the fact that I placed only #188 out of 400 in the rankings. In another post, I will explain how researchers can move up in the rankings. Of course, one way to move up in the rankings is to increase statistical power in future studies. The rankings will be updated again when the 2021 data are available.

Despite the preliminary nature, I am confident that the results provide valuable information. Until know all p-values below .05 have been treated as if they are equally informative. The rankings here show that this is not the case. While p = .02 can be informative for one researcher, p = .002 may still entail a high false discovery risk for another researcher.

Good science requires not only open and objective reporting of new data; it also requires unbiased review of the literature. However, there are no rules and regulations regarding citations, and many authors cherry-pick citations that are consistent with their claims. Even when studies have failed to replicate, original studies are cited without citing the replication failures. In some cases, authors even cite original articles that have been retracted. Fortunately, it is easy to spot these acts of unscientific behavior. Here I am starting a project to list examples of bad scientific behaviors. Hopefully, more scientists will take the time to hold their colleagues accountable for ethical behavior in citations. They can even do so by posting anonymously on the PubPeer comment site.

RankNameTestsODREDRERRFDRAlpha
1Robert A. Emmons538789901.05
2Allison L. Skinner2295981851.05
3David Matsumoto3788379851.05
4Linda J. Skitka5326875822.05
5Todd K. Shackelford3057775822.05
6Jonathan B. Freeman2745975812.05
7Virgil Zeigler-Hill5157274812.05
8Arthur A. Stone3107573812.05
9David P. Schmitt2077871772.05
10Emily A. Impett5497770762.05
11Paula Bressan628270762.05
12Kurt Gray4877969812.05
13Michael E. McCullough3346969782.05
14Kipling D. Williams8437569772.05
15John M. Zelenski1567169762.05
16Amy J. C. Cuddy2128368782.05
17Elke U. Weber3126968770.05
18Hilary B. Bergsieker4396768742.05
19Cameron Anderson6527167743.05
20Rachael E. Jack2497066803.05
21Jamil Zaki4307866763.05
22A. Janet Tomiyama767865763.05
23Benjamin R. Karney3925665733.05
24Phoebe C. Ellsworth6057465723.05
25Jim Sidanius4876965723.05
26Amelie Mummendey4617065723.05
27Carol D. Ryff2808464763.05
28Juliane Degner4356364713.05
29Steven J. Heine5977863773.05
30David M. Amodio5846663703.05
31Thomas N Bradbury3986163693.05
32Elaine Fox4727962783.05
33Miles Hewstone14277062733.05
34Linda R. Tropp3446561803.05
35Rainer Greifeneder9447561773.05
36Klaus Fiedler19507761743.05
37Jesse Graham3777060763.05
38Richard W. Robins2707660704.05
39Simine Vazire1376660644.05
40On Amir2676759884.05
41Edward P. Lemay2898759814.05
42William B. Swann Jr.10707859804.05
43Margaret S. Clark5057559774.05
44Bernhard Leidner7246459654.05
45B. Keith Payne8797158764.05
46Ximena B. Arriaga2846658694.05
47Joris Lammers7286958694.05
48Patricia G. Devine6067158674.05
49Rainer Reisenzein2016557694.05
50Barbara A. Mellers2878056784.05
51Joris Lammers7056956694.05
52Jean M. Twenge3817256594.05
53Nicholas Epley15047455724.05
54Kaiping Peng5667754754.05
55Krishna Savani6387153695.05
56Leslie Ashburn-Nardo1098052835.05
57Lee Jussim2268052715.05
58Richard M. Ryan9987852695.05
59Ethan Kross6146652675.05
60Edward L. Deci2847952635.05
61Roger Giner-Sorolla6638151805.05
62Bertram F. Malle4227351755.05
63George A. Bonanno4797251705.05
64Jens B. Asendorpf2537451695.05
65Samuel D. Gosling1085851625.05
66Tessa V. West6917151595.05
67Paul Rozin4497850845.05
68Joachim I. Krueger4367850815.05
69Sheena S. Iyengar2076350805.05
70James J. Gross11047250775.05
71Mark Rubin3066850755.05
72Pieter Van Dessel5787050755.05
73Shinobu Kitayama9837650715.05
74Matthew J. Hornsey16567450715.05
75Janice R. Kelly3667550705.05
76Antonio L. Freitas2477950645.05
77Paul K. Piff1667750635.05
78Mina Cikara3927149805.05
79Beate Seibt3797249626.01
80Ludwin E. Molina1636949615.05
81Bertram Gawronski18037248766.01
82Penelope Lockwood4587148706.01
83Edward R. Hirt10428148656.01
84Matthew D. Lieberman3987247806.01
85John T. Cacioppo4387647696.01
86Agneta H. Fischer9527547696.01
87Leaf van Boven7117247676.01
88Stephanie A. Fryberg2486247666.01
89Daniel M. Wegner6027647656.01
90Anne E. Wilson7857147646.01
91Rainer Banse4027846726.01
92Alice H. Eagly3307546716.01
93Jeanne L. Tsai12417346676.01
94Jennifer S. Lerner1818046616.01
95Andrea L. Meltzer5495245726.01
96R. Chris Fraley6427045727.01
97Constantine Sedikides25667145706.01
98Paul Slovic3777445706.01
99Dacher Keltner12337245646.01
100Brian A. Nosek8166844817.01
101George Loewenstein7527144727.01
102Ursula Hess7747844717.01
103Jason P. Mitchell6007343737.01
104Jessica L. Tracy6327443717.01
105Charles M. Judd10547643687.01
106S. Alexander Haslam11987243647.01
107Mark Schaller5657343617.01
108Susan T. Fiske9117842747.01
109Lisa Feldman Barrett6446942707.01
110Jolanda Jetten19567342677.01
111Mario Mikulincer9018942647.01
112Bernadette Park9737742647.01
113Paul A. M. Van Lange10927042637.01
114Wendi L. Gardner7986742637.01
115Will M. Gervais1106942597.01
116Jordan B. Peterson2666041797.01
117Philip E. Tetlock5497941737.01
118Amanda B. Diekman4388341707.01
119Daniel H. J. Wigboldus4927641678.01
120Michael Inzlicht6866641638.01
121Naomi Ellemers23887441638.01
122Phillip Atiba Goff2996841627.01
123Stacey Sinclair3277041578.01
124Francesca Gino25217540698.01
125Michael I. Norton11367140698.01
126David J. Hauser1567440688.01
127Elizabeth Page-Gould4115740668.01
128Tiffany A. Ito3498040648.01
129Richard E. Petty27716940648.01
130Tim Wildschut13747340648.01
131Norbert Schwarz13377240638.01
132Veronika Job3627040638.01
133Wendy Wood4627540628.01
134Minah H. Jung1568339838.01
135Marcel Zeelenberg8687639798.01
136Tobias Greitemeyer17377239678.01
137Jason E. Plaks5827039678.01
138Carol S. Dweck10287039638.01
139Christian S. Crandall3627539598.01
140Harry T. Reis9986938749.01
141Vanessa K. Bohns4207738748.01
142Jerry Suls4137138688.01
143Eric D. Knowles3846838648.01
144C. Nathan DeWall13367338639.01
145Clayton R. Critcher6978238639.01
146John F. Dovidio20196938629.01
147Joshua Correll5496138629.01
148Abigail A. Scholer5565838629.01
149Chris Janiszewski1078138589.01
150Herbert Bless5867338579.01
151Mahzarin R. Banaji8807337789.01
152Rolf Reber2806437729.01
153Kevin N. Ochsner4067937709.01
154Mark J. Brandt2777037709.01
155Geoff MacDonald4066737679.01
156Mara Mather10387837679.01
157Antony S. R. Manstead16567237629.01
158Lorne Campbell4336737619.01
159Sanford E. DeVoe2367137619.01
160Ayelet Fishbach14167837599.01
161Fritz Strack6077537569.01
162Jeff T. Larsen18174366710.01
163Nyla R. Branscombe12767036659.01
164Yaacov Schul4116136649.01
165D. S. Moskowitz34187436639.01
166Pablo Brinol13566736629.01
167Todd B. Kashdan3777336619.01
168Barbara L. Fredrickson2877236619.01
169Duane T. Wegener9807736609.01
170Joanne V. Wood10937436609.01
171Daniel A. Effron4846636609.01
172Niall Bolger3766736589.01
173Craig A. Anderson4677636559.01
174Michael Harris Bond37873358410.01
175Glenn Adams27071357310.01
176Daniel M. Bernstein40473357010.01
177C. Miguel Brendl12176356810.01
178Azim F. Sharif18374356810.01
179Emily Balcetis59969356810.01
180Eva Walther49382356610.01
181Michael D. Robinson138878356610.01
182Igor Grossmann20364356610.01
183Diana I. Tamir15662356210.01
184Samuel L. Gaertner32175356110.01
185John T. Jost79470356110.01
186Eric L. Uhlmann45767356110.01
187Nalini Ambady125662355610.01
188Daphna Oyserman44655355410.01
189Victoria M. Esses29575355310.01
190Linda J. Levine49574347810.01
191Wiebke Bleidorn9963347410.01
192Thomas Gilovich119380346910.01
193Alexander J. Rothman13369346510.01
194Francis J. Flynn37872346310.01
195Paula M. Niedenthal52269346110.01
196Ozlem Ayduk54962345910.01
197Paul Ekman8870345510.01
198Alison Ledgerwood21475345410.01
199Christopher R. Agnew32575337610.01
200Michelle N. Shiota24260336311.01
201Malte Friese50161335711.01
202Kerry Kawakami48768335610.01
203Danu Anthony Stinson49477335411.01
204Jennifer A. Richeson83167335211.01
205Margo J. Monteith77376327711.01
206Ulrich Schimmack31875326311.01
207Mark Snyder56272326311.01
208Michele J. Gelfand36576326311.01
209Russell H. Fazio109469326111.01
210Eric van Dijk23867326011.01
211Tom Meyvis37777326011.01
212Eli J. Finkel139262325711.01
213Robert B. Cialdini37972325611.01
214Jonathan W. Kunstman43066325311.01
215Delroy L. Paulhus12177318212.01
216Yuen J. Huo13274318011.01
217Gerd Bohner51371317011.01
218Christopher K. Hsee68975316311.01
219Vivian Zayas25171316012.01
220John A. Bargh65172315512.01
221Tom Pyszczynski94869315412.01
222Roy F. Baumeister244269315212.01
223E. Ashby Plant83177315111.01
224Kathleen D. Vohs94468315112.01
225Jamie Arndt131869315012.01
226Anthony G. Greenwald35772308312.01
227Nicholas O. Rule129468307513.01
228Lauren J. Human44759307012.01
229Jennifer Crocker51568306712.01
230Dale T. Miller52171306412.01
231Thomas W. Schubert35370306012.01
232Joseph A. Vandello49473306012.01
233W. Keith Campbell52870305812.01
234Arthur Aron30765305612.01
235Pamela K. Smith14966305212.01
236Aaron C. Kay132070305112.01
237Steven W. Gangestad19863304113.005
238Eliot R. Smith44579297313.01
239Nir Halevy26268297213.01
240E. Allan Lind37082297213.01
241Richard E. Nisbett31973296913.01
242Hazel Rose Markus67476296813.01
243Emanuele Castano44569296513.01
244Dirk Wentura83065296413.01
245Boris Egloff27481295813.01
246Monica Biernat81377295713.01
247Gordon B. Moskowitz37472295713.01
248Russell Spears228673295513.01
249Jeff Greenberg135877295413.01
250Caryl E. Rusbult21860295413.01
251Naomi I. Eisenberger17974287914.01
252Brent W. Roberts56272287714.01
253Yoav Bar-Anan52575287613.01
254Eddie Harmon-Jones73873287014.01
255Matthew Feinberg29577286914.01
256Roland Neumann25877286713.01
257Eugene M. Caruso82275286413.01
258Ulrich Kuehnen82275286413.01
259Elizabeth W. Dunn39575286414.01
260Jeffry A. Simpson69774285513.01
261Sander L. Koole76765285214.01
262Richard J. Davidson38064285114.01
263Shelly L. Gable36464285014.01
264Adam D. Galinsky215470284913.01
265Grainne M. Fitzsimons58568284914.01
266Geoffrey J. Leonardelli29068284814.005
267Joshua Aronson18385284614.005
268Henk Aarts100367284514.005
269Vanessa K. Bohns42276277415.01
270Jan De Houwer197270277214.01
271Dan Ariely60070276914.01
272Charles Stangor18581276815.01
273Karl Christoph Klauer80167276514.01
274Mario Gollwitzer50058276214.01
275Jennifer S. Beer8056275414.01
276Eldar Shafir10778275114.01
277Guido H. E. Gendolla42276274714.005
278Klaus R. Scherer46783267815.01
279William G. Graziano53271266615.01
280Galen V. Bodenhausen58574266115.01
281Sonja Lyubomirsky53071265915.01
282Kai Sassenberg87271265615.01
283Kristin Laurin64863265115.01
284Claude M. Steele43473264215.005
285David G. Rand39270258115.01
286Paul Bloom50272257916.01
287Kerri L. Johnson53276257615.01
288Batja Mesquita41671257316.01
289Rebecca J. Schlegel26167257115.01
290Phillip R. Shaver56681257116.01
291David Dunning81874257016.01
292Laurie A. Rudman48272256816.01
293David A. Lishner10565256316.01
294Mark J. Landau95078254516.005
295Ronald S. Friedman18379254416.005
296Joel Cooper25772253916.005
297Alison L. Chasteen22368246916.01
298Jeff Galak31373246817.01
299Steven J. Sherman88874246216.01
300Shigehiro Oishi110964246117.01
301Thomas Mussweiler60470244317.005
302Mark W. Baldwin24772244117.005
303Evan P. Apfelbaum25662244117.005
304Nurit Shnabel56476237818.01
305Klaus Rothermund73871237618.01
306Felicia Pratto41073237518.01
307Jonathan Haidt36876237317.01
308Roland Imhoff36574237318.01
309Jeffrey W Sherman99268237117.01
310Jennifer L. Eberhardt20271236218.005
311Bernard A. Nijstad69371235218.005
312Brandon J. Schmeichel65266234517.005
313Sam J. Maglio32572234217.005
314David M. Buss46182228019.01
315Yoel Inbar28067227119.01
316Serena Chen86572226719.005
317Spike W. S. Lee14568226419.005
318Marilynn B. Brewer31475226218.005
319Michael Ross116470226218.005
320Dieter Frey153868225818.005
321G. Daniel Lassiter18982225519.01
322Sean M. McCrea58473225419.005
323Wendy Berry Mendes96568224419.005
324Paul W. Eastwick58365216919.005
325Kees van den Bos115084216920.005
326Maya Tamir134280216419.005
327Joseph P. Forgas88883215919.005
328Michaela Wanke36274215919.005
329Dolores Albarracin54066215620.005
330Elizabeth Levy Paluck3184215520.005
331Vanessa LoBue29968207621.01
332Christopher J. Armitage16062207321.005
333Elizabeth A. Phelps68678207221.005
334Jay J. van Bavel43764207121.005
335David A. Pizarro22771206921.005
336Andrew J. Elliot101881206721.005
337William A. Cunningham23876206422.005
338Laura D. Scherer21269206421.01
339Kentaro Fujita45869206221.005
340Geoffrey L. Cohen159068205021.005
341Ana Guinote37876204721.005
342Tanya L. Chartrand42467203321.001
343Selin Kesebir32866197322.005
344Vincent Y. Yzerbyt141273197322.01
345James K. McNulty104756196523.005
346Robert S. Wyer87182196322.005
347Travis Proulx17463196222.005
348Peter M. Gollwitzer130364195822.005
349Nilanjana Dasgupta38376195222.005
350Jamie L. Goldenberg56877195022.01
351Richard P. Eibach75369194723.001
352Gerald L. Clore45674194522.001
353James M. Tyler13087187424.005
354Roland Deutsch36578187124.005
355Ed Diener49864186824.005
356Kennon M. Sheldon69874186623.005
357Wilhelm Hofmann62467186623.005
358Laura L. Carstensen72377186424.005
359Toni Schmader54669186124.005
360Frank D. Fincham73469185924.005
361David K. Sherman112861185724.005
362Lisa K. Libby41865185424.005
363Chen-Bo Zhong32768184925.005
364Stefan C. Schmukle11462177126.005
365Michel Tuan Pham24686176825.005
366Leandre R. Fabrigar63270176726.005
367Neal J. Roese36864176525.005
368Carey K. Morewedge63376176526.005
369Timothy D. Wilson79865176326.005
370Brad J. Bushman89774176225.005
371Ara Norenzayan22572176125.005
372Benoit Monin63565175625.005
373Michael W. Kraus61772175526.005
374Ad van Knippenberg68372175526.001
375E. Tory. Higgins186868175425.001
376Ap Dijksterhuis75068175426.005
377Joseph Cesario14662174526.001
378Simone Schnall27062173126.001
379Joshua M. Ackerman38053167013.01
380Melissa J. Ferguson116372166927.005
381Laura A. King39176166829.005
382Daniel T. Gilbert72465166527.005
383Charles S. Carver15482166428.005
384Leif D. Nelson40974166428.005
385David DeSteno20183165728.005
386Sandra L. Murray69760165528.001
387Heejung S. Kim85859165529.001
388Mark P. Zanna65964164828.001
389Nira Liberman130475156531.005
390Gun R. Semin15979156429.005
391Tal Eyal43962156229.005
392Nathaniel M Lambert45666155930.001
393Angela L. Duckworth12261155530.005
394Dana R. Carney20060155330.001
395Garriy Shteynberg16854153130.005
396Lee Ross34977146331.001
397Arie W. Kruglanski122878145833.001
398Ziva Kunda21767145631.001
399Shelley E. Taylor42769145231.001
400Jon K. Maner104065145232.001
401Gabriele Oettingen104761144933.001
402Nicole L. Mead24070144633.01
403Gregory M. Walton58769144433.001
404Michael A. Olson34665136335.001
405Fiona Lee22167135834.001
406Melody M. Chao23757135836.001
407Adam L. Alter31478135436.001
408Sarah E. Hill50978135234.001
409Jaime L. Kurtz9155133837.001
410Michael A. Zarate12052133136.001
411Jennifer K. Bosson65976126440.001
412Daniel M. Oppenheimer19880126037.001
413Deborah A. Prentice8980125738.001
414Yaacov Trope127773125738.001
415Oscar Ybarra30563125540.001
416William von Hippel39865124840.001
417Steven J. Spencer54167124438.001
418Martie G. Haselton18673115443.001
419Shelly Chaiken36074115244.001
420Susan M. Andersen36174114843.001
421Dov Cohen64168114441.001
422Mark Muraven49652114441.001
423Ian McGregor40966114041.001
424Hans Ijzerman2145694651.001
425Linda M. Isbell1156494150.001
426Cheryl J. Wakslak2787383559.001

“Psychological Science” in 2020

Psychological Science, Replicability, Replicability-Ranking, Z-Curve

Psychological Science is the flagship journal of the Association for Psychological Science (APS). In response to the replication crisis, D. Stephen Lindsay worked hard to increase the credibility of results published in this journal as editor from 2014-2019 (Schimmack, 2020). This work paid off and meta-scientific evidence shows that publication bias decreased and replicability increased (Schimmack, 2020). In the replicability rankings, Psychological Science is one of a few journals that show reliable improvement over the past decade (Schimmack, 2020).

This year, Patricia J. Bauer took over as editor. Some meta-psychologists were concerned that replicability might be less of a priority because she did not embrace initiatives like preregistration (New Psychological Science Editor Plans to Further Expand the Journal’s Reach).

The good news is that these concerns were unfounded. The meta-scientific criteria of credibility did not change notably from 2019 to 2020.

The observed discovery rates were 64% in 2019 and 66% in 2020. The estimated discovery rates were 58% in 2019 and 59%, respectively. Visual inspection of the z-curves and the slightly higher ODR than EDR suggests that there is still some selection for significant result. That is, researchers use so-called questionable research practices to produce statistically significant results. However, the magnitude of these questionable research practices is small and much lower than in 2010 (ODR = 77%, EDR = 38%).

Based on the EDR, it is possible to estimate the maximum false discovery rate (i.e., the percentage of significant results where the null-hypothesis is true). This rate is low with 4% in both years. Even the upper limit of the 95%CI is only 12%. This contradicts the widespread concern that most published (significant) results are false (Ioannidis, 2005).

The expected replication rate is slightly, but not significantly (i.e., it could be just sampling error) lower in 2020 (76% vs. 83%). Given the small risk of a false positive result, this means that on average significant results were obtained with the recommended power of 80% (Cohen, 1988).

Overall, these results suggest that published results in Psychological Science are credible and replicable. However, this positive evaluations comes with a few caveats.

First, null-hypothesis significance testing can only provide information that there is an effect and the direction of the effect. It cannot provide information about the effect size. Moreover, it is not possible to use the point estimates of effect sizes in small samples to draw inferences about the actual population effect size. Often the 95% confidence interval will include small effect sizes that may have no practical significance. Readers should clearly evaluate the lower limit of the 95%CI to examine whether a practically significant effect was demonstrated.

Second, the replicability estimate of 80% is an average. The average power of results that are just significant is lower. The local power estimates below the x-axis suggest that results with z-scores between 2 and 3 (p < .05 & p > .005) have only 50% power. It is recommended to increase sample sizes for follow-up studies.

Third, the local power estimates also show that most non-significant results are false negatives (type-II errors). Z-scores between 1 and 2 are estimated to have 40% average power. It is unclear how often articles falsely infer that an effect does not exist or can be ignored because the test was not significant. Often sampling error alone is sufficient to explain differences between test statistics in the range from 1 to 2 and from 2 to 3.

Finally, 80% power is sufficient for a single focal test. However, with 80% power, multiple focal tests are likely to produce at least one non-significant result. If all focal tests are significant, there is a concern that questionable research practices were used (Schimmack, 2012).

Readers should also carefully examine the results of individual articles. The present results are based on automatic extraction of all statistical tests. If focal tests have only p-values in the range between .05 and .005, the results are less credible than if at least some p-values are below .005 (Schimmack, 2020).

In conclusion, Psychological Science has responded to concerns about a high rate of false positive results by increasing statistical power and reducing publication bias. This positive trend continued in 2020 under the leadership of the new editor Patricia Bauer.