Category Archives: Power

The Power-Corrected H-Index

I was going to write this blog post eventually, but the online first publication of Radosic and Diener’s (2021) article “Citation Metrics in Psychological Science” provided a good opportunity to do so now.

Radosic and Diener’s (2021) article’s main purpose was to “provide norms to help evaluate the citation counts of psychological scientists” (p. 1). The authors also specify the purpose of these evaluations. “Citation metrics are one source of information that can be used in hiring, promotion, awards, and funding, and our goal is to help these evaluations” (p. 1).

The authors caution readers that they are agnostic about the validity of citation counts as a measure of good science. “The merits and demerits of citation counts are beyond the scope of the current article” (p. 8). Yet, they suggest that “there is much to recommend citation numbers in evaluating scholarly records” (p. 11).

At the same time, they list some potential limitations of using citation metrics to evaluate researchers.

1. Articles that developed a scale can have high citation counts. For example, Ed Diener has over 71,000 citations. His most cited article is the 1985 article with his Satisfaction with Life Scale. With 12,000 citations, it accounts for 17% of his citations. The fact that articles that published a measure have such high citation counts reflects a problem in psychological science. Researchers continue to use the first measure that was developed for a new construct (e.g., Rosenberg’s 1965 self-esteem scale) instead of improving measurement which would lead to citations of newer articles. So, the high citation counts of articles with scales is a problem, but it is only a problem if citation counts are used as a metric. A better metric is the H-Index that takes number of publications and citations into account. Ed Diener also has a very high H-Index of 108 publications with 108 or more citations. His scale article is only of these articles. Thus, scale development articles are not a major problem.

2. Review articles are cited more heavily than original research articles. Once more, Ed Diener is a good example. His second and third most cited articles are the 1984 and the co-authored 1999 Psychological Bulletin review articles on subjective well-being that together account for another 9,000 citations (13%). However, even review articles are not a problem. First, they also are unlikely to have an undue influence on the H-Index and second it is possible to exclude review articles and to compute metrics only for empirical articles. Web of Science makes this very easy. In WebofScience 361 out of Diener’s 469 publications are listed as articles. The others are listed as reviews, book chapters, or meeting abstracts. With a click of a button, we can produce the citation metrics only for the 361 articles. The H-Index drops from 108 to 102. Careful hand-selection of articles is unlikely to change this.

3. Finally, Radosic and Diener (2021) mention large-scale collaborations as a problem. For example, one of the most important research projects in psychological science in the last decade was the Reproducibility Project that examined the replicability of psychological science with 100 replication studies (Open Science Collaboration, 2015). This project required a major effort by many researchers. Participation earned researchers over 2,000 citations in just five years and the article is likely to be the most cited article for many of the collaborators. I do not see this as a problem because large-scale collaborations are important and can produce results that no single lab can produce. Thus, high citation counts provide a good incentive to engage in these collaborations.

To conclude, Radosic and Diener’s article provides norms for a citation counts that can and will be used to evaluate psychological scientists. However, the article sidesteps the main question about the use of citation metrics, namely (a) what criteria should be used to evaluate scientists and (b) are citation metrics valid indicators of these criteria. In short, the article is just another example that psychologists develop and promote measures without examining their construct validity (Schimmack, 2021).

What is a good scientists?

I didn’t do an online study to examine the ideal prototype of a scientist, so I have to rely on my own image of a good scientist. A key criterion is to search for some objectively verifiable information that can inform our understanding of the world, or in psychology ourselves; that is, humans affect, behavior, and cognition – the ABC of psychology. The second criterion elaborates the term objective. Scientists use methods that produce the same results independent of the user of the methods. That is, studies should be reproducible and results should be replicable within the margins of error. Third, the research question should have some significance beyond the personal interests of a scientist. This is of course a tricky criterion, but research that solves major problems like finding a vaccine for Covid-19 is more valuable and more likely to receive citations than research on the liking of cats versus dogs (I know, this is the most controversial statement I am making; go cats!). The problem is that not everybody can do research that is equally important to a large number of people. Once more Ed Diener is a good example. In the 1980s, he decided to study human happiness, which was not a major topic in psychology. Ed Diener’s high H-Index reflects his choice of a topic that is of interest to pretty much everybody. In contrast, research on stigma of minority groups is not of interest to a large group of people and unlikely to attract the same amount of attention. Thus, a blind focus on citation metrics is likely to lead to research on general topics and avoid research that applies research to specific problems. The problem is clearly visible in research on prejudice, where the past 20 years have produced hundreds of studies with button-press tasks by White researchers with White participants that gobbled up funding that could have been used for BIBOC researchers to study the actual issues in BIPOC populations. In short, relevance and significance of research is very difficult to evaluate, but it is unlikely to be reflected in citation metrics. Thus, a danger is that metrics are being used because they are easy to measure and relevance is not being used because it is harder to measure.

Do Citation Metrics Reward Good or Bad Research?

The main justification for the use of citation metrics is the hypothesis that the wisdom of crowds will lead to more citations of high quality work.

“The argument in favor of personal judgments overlooks the fact that citation counts are also based on judgments by scholars. In the case of citation counts, however, those judgments are broadly derived from the whole scholarly community and are weighted by the scholars who are publishing about the topic of the cited publications. Thus, there is much to recommend citation
numbers in evaluating scholarly records.” (Radosic & Diener, 2021, p. 8).

This statement is out of touch with discussions about psychological science over the past decade in the wake of the replication crisis (see Schimmack, 2020, for a review; I have to cite myself to get up my citation metrics. LOL). In order to get published and cited, researchers of original research articles in psychological science need statistically significant p-values. The problem is that it can be difficult to find significant results when novel hypotheses are false or effect sizes are small. Given the pressure to publish in order to rise in the H-Index rankings, psychologists have learned to use a number of statistical tricks to get significant results in the absence of strong evidence in the data. These tricks are known as questionable research practices, but most researchers think they are acceptable (John et al., 2012). However, these practices undermine the value of significance testing and published results may be false positives or difficult to replicate, and do not add to the progress of science. Thus, citation metrics may have the negative consequence to pressure scientists into using bad practices and to reward scientists who publish more false results just because they publish more.

Meta-psychologists have produced strong evidence that the use of these practices was widespread and accounts for the majority of replication failures that occurred over the past decade.

Schimmack, U. (2020). A meta-psychological perspective on the decade of replication failures in social psychology. Canadian Psychology/Psychologie canadienne, 61(4), 364–376.

Motyl et al. (2017) collected focal test statistics from a representative sample of articles in social psychology. I analyzed their data using z-curve.2.0 (Brunner & Schimmack, 2020; Bartos & Schimmack, 2021). Figure 1 shows the distribution of the test-statistics after converting them into absolute z-scores, where higher values show a higher signal/noise (effect size / sampling error) ratio. A z-score of 1.96 is needed to claim a discovery with p < .05 (two-sided). Consistent with publication practices since the 1960s, most focal hypothesis tests confirm predictions (Sterling, 1959). The observed discovery rate is 90% and even higher if marginally significant results are included (z > 1.65). This high success rate is not something to celebrate. Even I could win all marathons if I use a short-cut and run only 5km. The problem with this high success rate is clearly visible when we fit a model to the distribution of the significant z-scores and extrapolate the distribution of z-scores that are not significant (the blue curve in the figure). Based on this distribution, the significant results are only 19% of all tests, indicating that many more non-significant results are expected than observed. The discrepancy between the observed and estimated discovery rate provides some indication of the use of questionable research practices. Moreover, the estimated discovery rate shows how much statistical power studies have to produce significant results without questionable research practices. The results confirm suspicions that power in social psychology is abysmally low (Cohen, 1961; Tversky & Kahneman, 1971).

The use of questionable practices makes it possible that citation metrics may be invalid. When everybody in a research field uses p < .05 as a criterion to evaluate manuscripts and these p-values are obtained with questionable research practices, the system will reward researchers how use the most questionable methods to produce more questionable results than their peers. In other words, citation metrics are no longer a valid criterion of research quality. Instead, bad research is selected and rewarded (Smaldino & McElreath, 2016). However, it is also possible that implicit knowledge helps researchers to focus on robust results and that questionable research practices are not rewarded. For example, prediction markets suggest that it is fairly easy to spot shoddy research and to predict replication failures (Dreber et al., 2015). Thus, we cannot assume that citation metrics are valid or invalid. Instead, citation metrics – like all measures – require a program of construct validation.

Do Citation Metrics Take Statistical Power Into Account?

A few days ago, I published the first results of an ongoing research project that examines the relationship between researchers’ citation metrics and estimates of the average power of their studies based on z-curve analyses like the one shown in Figure 1 (see Schimmack, 2021, for details). The key finding is that there is no statistically or practically significant relationship between researchers H-Index and the average power of their studies. Thus, researchers who invest a lot of resources in their studies to produce results with a low false positive risk and high replicability are not cited more than researchers who flood journals with low powered studies that produce questionable results that are difficult to replicate.

These results show a major problem of citation metrics. Although methodologists have warned against underpowered studies, researchers have continued to use underpowered studies because they can use questionable practices to produce the desired outcome. This strategy is beneficial for scientists and their career, but hurts the larger goal of science to produce a credible body of knowledge. This does not mean that we need to abandon citation metrics altogether, but it must be complemented with other information that reflects the quality of researchers data.

The Power-Corrected H-Index

In my 2020 review article, I proposed to weight the H-Index by estimates of researchers’ replicability. For my illustration, I used the estimated replication rate, which is the average power of significant tests, p < .05 (Brunner & Schimmack, 2020). One advantage of the ERR is that it is highly reliable. The reliability of the ERRs for 300 social psychologists is .90. However, the ERR has some limitations. First, it predicts replication outcomes under the unrealistic assumption that psychological studies can be replicated exactly. However, it has been pointed out that this often impossible, especially in social psychology (Strobe & Strack, 2014). As a result, ERR predictions are overly optimistic and overestimate the success rate of actual replication studies (Bartos & Schimmack, 2021). In contrast, EDR estimates are much more in line with actual replication outcomes because effect sizes in replication studies can regress towards the mean. For example, Figure 1 shows an EDR of 19% for social psychology and the actual success rate (if we can call it that) for social psychology was 25% in the reproducibility project (Open Science Collaboration, 2015). Another advantage of the EDR is that it is sensitive to questionable research practices that tend to produce an abundance of p-values that are just significant. Thus, the EDR more strongly punishes researchers for using these undesirable practices. The main limitation of the EDR is that it is less reliable than the ERR. The reliability for 300 social psychologists was only .5. Of course, it is not necessary to chose between ERR and EDR. Just like there are many citation metrics, it is possible to evaluate the pattern of power-corrected metrics using ERR and EDR. I am presenting both values here, but the rankings are sorted by EDR weighted H-Indices.

The H-Index is an absolute number that can range from 0 to infinity. In contrast, power is limited to a range from 5% (with alpha = .05) to 100%. Thus, it makes sense to use power as a weight and to weight the H-index by a researchers EDR. A researcher who published only studies with 100% power has a power-corrected H-Index that is equivalent to the actual H-Index. The average EDR of social psychologists, however, is 35%. Thus, the average H-index is reduced to a third of the unadjusted value.

To illustrate this approach, I am using two researchers with a large H-Index, but different EDRs. One researcher is James J. Gross with an H-Index of 99 in WebofScience. His z-curve plot shows some evidence that questionable research practices were used to report 72% significant results with 50% power. However, the 95%CI around the EDR ranges from 23% to 78% and includes the point estimate. Thus, the evidence for QRPs is weak and not statistically significant. More important, the EDR -corrected H-Index is 90 * .50 = 45.

A different example is provided by Shelly E. Taylor with a similarly high H-Index of 84, but her z-curve plot shows clear evidence that the observed discovery rate is inflated by questionable research practices. Her low EDR reduces the H-Index considerably and results in a PC-H-Index of only 12.6.

Weighing the two researchers’ H-Index by their respective ERR’s, 77 vs. 54, has similar, but less extreme effects in absolute terms, ERR-adjusted H-Indices of 76 vs. 45.

In the sample of 300 social psychologists, the H-Index (r = .74) and the EDR (r = .65) contribute about equal amounts of variance to the power-corrected H-Index. Of course, a different formula could be used to weigh power more or less.


Ed Diener is best known for his efforts to measure well-being and to point out that traditional economic indicators of well-being are imperfect. While wealth of countries is a strong predictor of citizens’ average well-being, r ~ .8, income is a poor predictor of individuals’ well-being with countries. However, economists continue to rely on income and GDP because it is more easily quantified and counted than subjective life-evaluations. Ironically, Diener advocates the opposite approach when it comes to measuring research quality. Counting articles and citations is relatively easy and objective, but it may not measure what we really want to measure, namely how much is somebody contributing to the advancement of knowledge. The construct of scientific advancement is probably as difficult to define as well-being, but producing replicable results with reproducible studies is one important criterion of good science. At present, citation metrics fail to track this indicator of research quality. Z-curve analyses of published results make it possible to measure this aspect of good science and I recommend to take it into account when researchers are being evaluated.

However, I do not recommend the use of quantitative information for the evaluation of hiring and promotion decisions. The reward system in science is too biased to reward privileged upper-class, White, US Americans (see APS rising stars lists). That being said, a close examination of published articles can be used to detect and eliminate researchers who severely p-hacked to get their significant results. Open science criteria can also be used to evaluate researchers who are just starting their career.

In conclusion, Radosic and Diener’s (2021) article disappointed me because it sidesteps the fundamental questions about the validity of citation metrics as a criterion for scientific excellence.

Conflict of Interest Statement: At the beginning of my career I was motivated to succeed in psychological science by publishing as many JPSP articles as possible and I made the unhealthy mistake to try to compete with Ed Diener. That didn’t work out for me. Maybe I am just biased against citation metrics because my work is not cited as much as I would like. Alternatively, my disillusionment with the system reflects some real problems with the reward structure in psychological science and helped me to see the light. The goal of science cannot be to have the most articles or the most citations, if these metrics do not really reflect scientific contributions. Chasing indicators is a trap, just like chasing happiness is a trap. Most scientists can hope to make maybe one lasting contribution to the advancement of knowledge. You need to please others to stay in the game, but beyond those minimum requirements to get tenure, personal criteria of success are better than social comparisons for the well-being of science and scientists. The only criterion that is healthy is to maximize statistical power. As Cohen said, less is more and by this criterion psychology is not doing well as more and more research is published with little concern about quality.

James J. Gross5076995077
John T. Cacioppo48701024769
Richard M. Ryan4661895269
Robert A. Emmons3940468588
Edward L. Deci3643695263
Richard W. Robins3440576070
Jean M. Twenge3335595659
William B. Swann Jr.3244555980
Matthew D. Lieberman3154674780
Roy F. Baumeister31531013152
David Matsumoto3133397985
Carol D. Ryff3136486476
Dacher Keltner3144684564
Michael E. McCullough3034446978
Kipling D. Williams3034446977
Thomas N Bradbury3033486369
Richard J. Davidson30551082851
Phoebe C. Ellsworth3033466572
Mario Mikulincer3045714264
Richard E. Petty3047744064
Paul Rozin2949585084
Lisa Feldman Barrett2948694270
Constantine Sedikides2844634570
Alice H. Eagly2843614671
Susan T. Fiske2849664274
Jim Sidanius2730426572
Samuel D. Gosling2733535162
S. Alexander Haslam2740624364
Carol S. Dweck2642663963
Mahzarin R. Banaji2553683778
Brian A. Nosek2546574481
John F. Dovidio2541663862
Daniel M. Wegner2434524765
Benjamin R. Karney2427376573
Linda J. Skitka2426327582
Jerry Suls2443633868
Steven J. Heine2328376377
Klaus Fiedler2328386174
Jamil Zaki2327356676
Charles M. Judd2336534368
Jonathan B. Freeman2324307581
Shinobu Kitayama2332455071
Norbert Schwarz2235564063
Antony S. R. Manstead2237593762
Patricia G. Devine2125375867
David P. Schmitt2123307177
Craig A. Anderson2132593655
Jeff Greenberg2139732954
Kevin N. Ochsner2140573770
Jens B. Asendorpf2128415169
David M. Amodio2123336370
Bertram Gawronski2133434876
Fritz Strack2031553756
Virgil Zeigler-Hill2022277481
Nalini Ambady2032573556
John A. Bargh2035633155
Arthur Aron2036653056
Mark Snyder1938603263
Adam D. Galinsky1933682849
Tom Pyszczynski1933613154
Barbara L. Fredrickson1932523661
Hazel Rose Markus1944642968
Mark Schaller1826434361
Philip E. Tetlock1833454173
Anthony G. Greenwald1851613083
Ed Diener18691011868
Cameron Anderson1820276774
Michael Inzlicht1828444163
Barbara A. Mellers1825325678
Margaret S. Clark1823305977
Ethan Kross1823345267
Nyla R. Branscombe1832493665
Jason P. Mitchell1830414373
Ursula Hess1828404471
R. Chris Fraley1828394572
Emily A. Impett1819257076
B. Keith Payne1723305876
Eddie Harmon-Jones1743622870
Wendy Wood1727434062
John T. Jost1730493561
C. Nathan DeWall1728453863
Thomas Gilovich1735503469
Elaine Fox1721276278
Brent W. Roberts1745592877
Harry T. Reis1632433874
Robert B. Cialdini1629513256
Phillip R. Shaver1646652571
Daphna Oyserman1625463554
Russell H. Fazio1631503261
Jordan B. Peterson1631394179
Bernadette Park1624384264
Paul A. M. Van Lange1624384263
Jeffry A. Simpson1631572855
Russell Spears1529522955
A. Janet Tomiyama1517236576
Jan De Houwer1540552772
Samuel L. Gaertner1526423561
Michael Harris Bond1535423584
Agneta H. Fischer1521314769
Delroy L. Paulhus1539473182
Marcel Zeelenberg1429373979
Eli J. Finkel1426453257
Jennifer Crocker1432483067
Steven W. Gangestad1420483041
Michael D. Robinson1427413566
Nicholas Epley1419265572
David M. Buss1452652280
Naomi I. Eisenberger1440512879
Andrew J. Elliot1448712067
Steven J. Sherman1437592462
Christian S. Crandall1421363959
Kathleen D. Vohs1423453151
Jamie Arndt1423453150
John M. Zelenski1415206976
Jessica L. Tracy1423324371
Gordon B. Moskowitz1427472957
Klaus R. Scherer1441522678
Ayelet Fishbach1321363759
Jennifer A. Richeson1321403352
Charles S. Carver1352811664
Leaf van Boven1318274767
Shelley E. Taylor1244841452
Lee Jussim1217245271
Edward R. Hirt1217264865
Shigehiro Oishi1232522461
Richard E. Nisbett1230432969
Kurt Gray1215186981
Stacey Sinclair1217304157
Niall Bolger1220343658
Paula M. Niedenthal1222363461
Eliot R. Smith1231422973
Tobias Greitemeyer1221313967
Rainer Reisenzein1214215769
Rainer Banse1219264672
Galen V. Bodenhausen1228462661
Ozlem Ayduk1221353459
E. Tory. Higgins1238701754
D. S. Moskowitz1221333663
Dale T. Miller1225393064
Jeanne L. Tsai1217254667
Roger Giner-Sorolla1118225180
Edward P. Lemay1115195981
Ulrich Schimmack1122353263
E. Ashby Plant1118363151
Ximena B. Arriaga1113195869
Janice R. Kelly1115225070
Frank D. Fincham1135601859
David Dunning1130432570
Boris Egloff1121372958
Karl Christoph Klauer1125392765
Caryl E. Rusbult1019362954
Tessa V. West1012205159
Jennifer S. Lerner1013224661
Wendi L. Gardner1015244263
Mark P. Zanna1030621648
Michael Ross1028452262
Jonathan Haidt1031432373
Sonja Lyubomirsky1022382659
Sander L. Koole1018352852
Duane T. Wegener1016273660
Marilynn B. Brewer1027442262
Christopher K. Hsee1020313163
Sheena S. Iyengar1015195080
Laurie A. Rudman1026382568
Joanne V. Wood916263660
Thomas Mussweiler917392443
Shelly L. Gable917332850
Felicia Pratto930402375
Wiebke Bleidorn920273474
Jeff T. Larsen917253667
Nicholas O. Rule923303075
Dirk Wentura920312964
Klaus Rothermund930392376
Joris Lammers911165669
Stephanie A. Fryberg913194766
Robert S. Wyer930471963
Mina Cikara914184980
Tiffany A. Ito914224064
Joel Cooper914352539
Joshua Correll914233862
Peter M. Gollwitzer927461958
Brad J. Bushman932511762
Kennon M. Sheldon932481866
Malte Friese915263357
Dieter Frey923392258
Lorne Campbell914233761
Monica Biernat817292957
Aaron C. Kay814283051
Yaacov Schul815233664
Joseph P. Forgas823392159
Guido H. E. Gendolla814302747
Claude M. Steele813312642
Igor Grossmann815233566
Paul K. Piff810165063
Joshua Aronson813282846
William G. Graziano820302666
Azim F. Sharif815223568
Juliane Degner89126471
Margo J. Monteith818243277
Timothy D. Wilson828451763
Kerry Kawakami813233356
Hilary B. Bergsieker78116874
Gerald L. Clore718391945
Phillip Atiba Goff711184162
Elizabeth W. Dunn717262864
Bernard A. Nijstad716312352
Mark J. Landau713282545
Christopher R. Agnew716213376
Brandon J. Schmeichel714302345
Arie W. Kruglanski728491458
Eric D. Knowles712183864
Yaacov Trope732571257
Wendy Berry Mendes714312244
Jennifer S. Beer714252754
Nira Liberman729451565
Penelope Lockwood710144870
Jeffrey W Sherman721292371
Geoff MacDonald712183767
Eva Walther713193566
Daniel T. Gilbert727411665
Grainne M. Fitzsimons611232849
Elizabeth Page-Gould611164066
Mark J. Brandt612173770
Ap Dijksterhuis620371754
James K. McNulty621331965
Dolores Albarracin618331956
Maya Tamir619292164
Jon K. Maner622431452
Alison L. Chasteen617252469
Jay J. van Bavel621302071
William A. Cunningham619302064
Glenn Adams612173573
Wilhelm Hofmann622331866
Ludwin E. Molina67124961
Lee Ross626421463
Andrea L. Meltzer69134572
Jason E. Plaks610153967
Ara Norenzayan621341761
Batja Mesquita617232573
Tanya L. Chartrand69282033
Toni Schmader518301861
Abigail A. Scholer59143862
C. Miguel Brendl510153568
Emily Balcetis510153568
Diana I. Tamir59153562
Nir Halevy513182972
Alison Ledgerwood58153454
Yoav Bar-Anan514182876
Paul W. Eastwick517242169
Geoffrey L. Cohen513252050
Yuen J. Huo513163180
Benoit Monin516291756
Gabriele Oettingen517351449
Roland Imhoff515212373
Mark W. Baldwin58202441
Ronald S. Friedman58192544
Shelly Chaiken522431152
Kristin Laurin59182651
David A. Pizarro516232069
Michel Tuan Pham518271768
Amy J. C. Cuddy517241972
Gun R. Semin519301564
Laura A. King419281668
Yoel Inbar414202271
Nilanjana Dasgupta412231952
Kerri L. Johnson413172576
Roland Neumann410152867
Richard P. Eibach410221947
Roland Deutsch416231871
Michael W. Kraus413241755
Steven J. Spencer415341244
Gregory M. Walton413291444
Ana Guinote49202047
Sandra L. Murray414251655
Leif D. Nelson416251664
Heejung S. Kim414251655
Elizabeth Levy Paluck410192155
Jennifer L. Eberhardt411172362
Carey K. Morewedge415231765
Lauren J. Human49133070
Chen-Bo Zhong410211849
Ziva Kunda415271456
Geoffrey J. Leonardelli46132848
Danu Anthony Stinson46113354
Kentaro Fujita411182062
Leandre R. Fabrigar414211767
Melissa J. Ferguson415221669
Nathaniel M Lambert314231559
Matthew Feinberg38122869
Sean M. McCrea38152254
David A. Lishner38132563
William von Hippel313271248
Joseph Cesario39191745
Martie G. Haselton316291154
Daniel M. Oppenheimer316261260
Oscar Ybarra313241255
Simone Schnall35161731
Travis Proulx39141962
Spike W. S. Lee38122264
Dov Cohen311241144
Ian McGregor310241140
Dana R. Carney39171553
Mark Muraven310231144
Deborah A. Prentice312211257
Michael A. Olson211181363
Susan M. Andersen210211148
Sarah E. Hill29171352
Michael A. Zarate24141331
Lisa K. Libby25101854
Hans Ijzerman2818946
James M. Tyler1681874
Fiona Lee16101358


Open Science Collaboration (OSC). (2015). Estimating the reproducibility
of psychological science. Science, 349, aac4716.

Radosic, N., & Diener, E. (2021). Citation Metrics in Psychological Science. Perspectives on Psychological Science.

Schimmack, U. (2021). The validation crisis. Meta-psychology. in press

Schimmack, U. (2020). A meta-psychological perspective on the decade of replication failures in social psychology. Canadian Psychology/Psychologie canadienne, 61(4), 364–376.

Replicability Rankings 2010-2020

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]

Men are created equal, p-values are not.

Is there still something new to say about p-values? Yes, there is. Most discussions of p-values focus on a scenario where a researcher tests a new hypothesis computes a p-value and now has to interpret the result. The status quo follows Fisher’s – 100 year old – approach to compare the p-value to a value of .05. If the p-value is below .05 (two-sided), the inference is that the population effect size deviates from zero in the same direction as the observed effect in the sample. If the p-value is greater than .05 the results are deemed inconclusive.

This approach to the interpretation of the data assumes that we have no other information about our hypothesis or that we do not trust this information sufficiently to incorporate it in our inference about the population effect size. Over the past decade, Bayesian psychologists have argued that we should replace p-values with Bayes-Factors. The advantage of Bayes-Factors is that they can incorporate prior information to draw inferences from data. However, if no prior information is available, the use of Bayesian statistics may cause more harm than good. To use priors without prior information, Bayes-Factors are computed with generic, default priors that are not based on any information about a research question. Along with other problems of Bayes-Factors, this is not an appealing solution to the problem of p-values.

Here I introduce a new approach to the interpretation of p-values that has been called empirical Bayesian and has been successfully applied in genomics to control the field-wise false positive rate. That is, prior information does not rest on theoretical assumptions or default values, but rather on prior empirical information. The information that is used to interpret a new p-value is the distribution of prior p-values.

P-value distributions

Every study is a new study because it relies on a new sample of participants that produces sampling error that is independent of the previous studies. However, studies are not independent in other characteristics. A researcher who conducted a study with N = 40 participants is likely to have used similar sample sizes in previous studies. And a researcher who used N = 200 is also likely to have used larger sample sizes in previous studies. Researchers are also likely to use similar designs. Social psychologists, for example, prefer between-subject designs to better deceive their participants. Cognitive psychologists care less about deception and study simple behaviors that can be repeated hundreds of times within an hour. Thus, researchers who used a between-subject design are likely to have used a between-subject design in previous studies and researchers who used a within-subject design are likely to have used a within-subject design before. Researchers may also be chasing different effect sizes. Finally, researchers can differ in their willingness to take risks. Some may only test hypotheses that are derived from prior theories that have a high probability of being correct, whereas others may be willing to shoot for the moon. All of these consistent differences between researchers (i.e., sample size, effect size, research design) influence the unconditional statistical power of their studies, which is defined as the long-run probability of obtaining significant results, p < .05.

Over the past decade, in the wake of the replication crisis, interest in the distribution of p-values has increased dramatically. For example, one approach uses the distribution of significant p-values, which is known as p-curve analysis (Simonsohn et al., 2014). If p-values were obtained with questionable research practices when the null-hypothesis is true (p-hacking), the distribution of significant p-values is flat. Thus, if the distribution is monotonically decreasing from 0 to .05, the data have evidential value. Although p-curve analyses has been extended to estimate statistical power, simulation studies show that the p-curve algorithm is systematically biased when power varies across studies (Bartos & Schimmack, 2020; Brunner & Schimmack, 2020).

As shown in simulation studies, a better way to estimate power is z-curve (Bartos & Schimmack, 2020; Brunner & Schimmack, 2020). Here I show how z-curve analyses of prior p-values can be used to demonstrate that p-values from one researcher are not equal to p-values of other researchers when we take their prior research practices into account. By using this prior information, we can adjust the alpha level of individual researchers to take their research practices into account. To illustrate this use of z-curve, I first start with an illustration how different research practices influence p-value distributions.

Scenario 1: P-hacking

In the first scenario, we assume that a researcher only tests false hypotheses (i.e., the null-hypothesis is always true (Bem, 2011; Simonsohn et al., 2011). In theory, it would be easy to spot false positives because replication studies would produce produce 19 non-significant results for every significant one and significant ones would have different signs. However, questionable research practices lead to a pattern of results where only significant results in one direction are reported, which is the norm in psychology (Sterling, 1959, Sterling et al., 1995; Schimmack, 2012).

In a z-curve analysis, p-values are first converted into z-scores, z = -qnorm(p/2) with qnorm being the inverse normal function and p being a two-sided p-value. A z-curve plot shows the histogram of all z-scores, including non-significant ones (Figure 1).

Visual inspection of the z-curve plot shows that all 200 p-values are significant (on the right side of the criterion value z = 1.96). it also shows that the mode of the distribution as at the significance criterion. Most important, visual inspection shows a steep drop from the mode to the range of non-significant values. That is, while z = 1.96 is the most common value, z = 1.95 is never observed. This drop provides direct visual information that questionable research practices were used because normal sampling error cannot produce such dramatic changes in the distribution.

I am skipping the technical details how the z-curve model is fitted to the distribution of z-scores (Bartos & Schimmack, 2020). It is sufficient to know that the model is fitted to the distribution of significant z-scores with a limited number of model parameters that are equally spaced over the range of z-scores from 0 to 6 (7 parameters, z = 0, z = 1, z = 2, …. z = 6). The model gives different weights to these parameters to match the observed distribution. Based on these estimates, z-curve.2.0 computes several statistics that can be used to interpret single p-values that have been published or future p-values by the same researcher, assuming that the same research practices are used.

The most important statistic is the expected discovery rate (EDR), which corresponds to the average power of all studies that were conducted by a researcher. Importantly, the EDR is an estimate that is based on only the significant results, but makes predictions about the number of non-significant results. In this example with N = 200 participants, the EDR is 7%. Of course, we know that it really is only 5% because the expected discovery rate for true hypotheses that are tested with alpha = .05 is 5%. However, sampling error can introduce biases in our estimates. Nevertheless, even with only 200 observations, the estimate of 7% is relatively close to 5%. Thus, z-curve tells us something important about the way these p-values were obtained. They were obtained in studies with very low power that is close to the criterion value for a false positive result.

Z-curve uses bootstrap to compute confidence intervals around the point estimate of the EDR. the 95%CI ranges from 5% to 18%. As the interval includes 5%, we cannot reject the hypothesis that all tests were false positives (which in this scenario is also the correct conclusion). At the upper end we can see that mean power is low, even if some true hypotheses are being tested.

The EDR can be used for two purposes. First, it can be used to examine the extent of selection for significance by comparing the EDR to the observed discovery rate (ODR; Schimmack, 2012). The ODR is simply the percentage of significant results that was observed in the sample of p-values. In this case, this is 200 out of 200 or 100%. The discrepancy between the EDR of 7% and 100% is large and 100% is clearly outside the 95%CI of the EDR. Thus, we have strong evidence that questionable research practices were used, which we know to be true in this simulation because the 200 tests were selected from a much larger sample of 4,000 tests.

Most important for the use of z-curve to interpret p-values is the ability to estimate the maximum False Discovery Rate (Soric, 1989). The false discovery rate is the percentage of significant results that are false positives or type-I errors. The false discovery rate is often confused with alpha, the long-run probability of making a type-I error. The significance criterion ensures that no more than 5% of significant and non-significant results are false positives. When we test 4,000 false hypotheses (i.e., the null-hypothesis is true) were are not going to have more than 5% (4,000 * .05 = 200) false positive results. This is true in general and it is true in this example. However, when only significant results are published, it is easy to make the mistake to assume that no more than 5% of the published 200 results are false positives. This would be wrong because the 200 were selected to be significant and they are all false positives.

The false discovery rate is the percentage of significant results that are false positives. It no longer matters whether non-significant results are published or not. We are only concerned with the population of p-values that are below .05 (z > 1.96). In our example, the question is how many of the 200 significant results could be false positives. Soric (1989 demonstrated that the EDR limits the number of false positive discoveries. The more discoveries there are, the lower is the risk that discoveries are false. Using a simple formula, we can compute the maximum false discovery rate from the EDR.

FDR = (1/(EDR – 1)*(.05/.95), with alpha = .05

With an EDR of 7%, we obtained a maximum FDR of 68%. We know that the true FDR is 100%, thus, the estimate is too low. However, the reason is that sampling error can have dramatic effects on the FDR estimates when the EDR is low. With an EDR of 6%, the FDR estimate goes up to 82% and with an EDR estimate of 5% it is 100%. To take account of this uncertainty, we can use the 95%CI of the EDR to compute a 95%CI for the FDR estimate, 24% to 100%. Now we see that we cannot rule out that the FDR is 100%.

In short, scenario 1 introduced the use of p-value distributions to provide useful information about the risk that the published results are false discoveries. In this extreme example, we can dismiss the published p-values as inconclusive or as lacking in evidential value.

Scenario 2: The Typical Social Psychologist

It is difficult to estimate the typical effect size in a literature. However, a meta-analysis of meta-analyses suggested that the average effect size in social psychology is Cohen’s d = .4 (Richard et al., 2003). A smaller set of replication studies that did not select for significance estimated an effect size of d = .3 for social psychology (d = .2 for JPSP, d = .4 for Psych Science; Open Science Collaboration, 2015). The later estimate may include an unknown number of hypotheses where the null-hypothesis is true and the true effect size is zero. Thus, I used d = .4 as a reasonable effect size for true hypotheses in social psychology (see also LeBel, Campbell, & Loving, 2017).

It is also known that a rule of thumb in experimental social psychology was to allocate n = 20 participants to a condition, resulting in a sample size of N = 40 in studies with two groups. In a 2 x 2 design, the main effect would be tested with N = 80. However, to keep this scenario simple, I used d = .4 and N = 40 for true effects. This affords 23% power to obtain a significant result.

Finkel, Eastwick, and Reis (2017) argued that power of 25% is optimal if 75% of the hypotheses that are being tested are true. However, the assumption that 75% of hypotheses are true may be on the optimistic side. Wilson and Wixted (2018) suggested that the false discovery risk is closer to 50%. With 23% power for true hypotheses, this implies a false discovery rate of Given uncertainty about the actual false discovery rate in social psychology, I used a scenario with 50% true and 50% false hypotheses.

I kept the number of significant results at 200. To obtain 200 significant results with an equal number of true and false hypotheses, we need 1,428 tests. The 714 true hypotheses contribute 714*.23 = 164 true positives and the 714 false hypotheses produce 714*.05 = 36 false positive results; 164 + 36 = 200. This implies a false discovery rate of 36/200 = 18%. The true EDR is (714*.23+714*.05)/(714+714) = 14%.

The z-curve plot looks very similar to the previous plot, but they are not identical. Although the EDR estimate is higher, it still includes zero. The maximum FDR is well above the actual FDR of 18%, but the 95%CI includes the actual value of 18%.

A notable difference between Figure 1 and Figure 2 is the expected replication rate (ERR), which corresponds to the average power of significant p-values. It is called the estimated replication rate (ERR) because it predicts the percentage of significant results if the studies that were selected for significance were replicated exactly (Brunner & Schimmack, 2020). When power is heterogeneous, power of the studies with significant results is higher than power of studies with non-significant results (Brunner & Schimmack, 2020). In this case, with only two power values, the reason is that false positives have a much lower chance to be significant (5%) than true positives (23%). As a result, the average power of significant studies is higher than the average power of all studies. In this simulation, the true average power of significant studies is the weighted average of true and false positives with significant results, (164*.23 +36*.05)/(164+36) = 20%. Z-curve perfectly estimated this value.

Importantly, the 95% CI of the ERR, 11% to 34%, does not include zero. Thus, we can reject the null-hypotheses that all of the significant results are false positives based on the ERR. In other words, the significant results have evidential value. However, we do not know the composition of this average. It could be a large percentage of false positives and a few true hypotheses with high power or it could be many true positives with low power. We also do not know which of the 200 significant results is a true positive or a false positive. Thus, we would need to conduct replication studies to distinguish between true and false hypotheses. And given the low power, we would only have a 23% chance of successfully replicating a true positive result. This is exactly what happened with the reproducibility project. And the inconsistent results lead to debates and require further replications. Thus, we have real-world evidence how uninformative p-values are when they are obtained this way.

Social psychologists might argue that the use of small samples is justified because most hypotheses in psychology are true. Thus, we can use prior information to assume that significant results are true positives. However, this logic fails when social psychologists test false hypotheses. In this case, the observed distribution of p-values (Figure 1) is not that different from the distribution that is observed when most significant results are true positives that were obtained with low power (Figure 2). Thus, it is doubtful that this is really an optimal use of resources (Finkel et al., 2015). However, until recently this was the way experimental social psychologists conducted their research.

Scenario 3: Cohen’s Way

In 1962 (!), Cohen conducted a meta-analysis of statistical power in social psychology. The main finding was that studies had only a 50% chance to get significant results with a median effect size of d = .5. Cohen (1988) also recommended that researchers should plan studies to have 80% power. However, this recommendation was ignored.

To achieve 80% power with d = .4, researchers need N = 200 participants. Thus, the number of studies is reduced from 5 studies with N = 40 to one study with N = 200. As Finkel et al. (2017) point out, we can make more discoveries with many small studies than a few large ones. However, this ignores that the results of the small studies are difficult to replicate. This was not a concern when social psychologists did not bother to test whether their discoveries are false discoveries or whether they can be replicated. The replication crisis shows the problems of this approach. Now we have results from decades of research that produced significant p-values without providing any information whether these significant results are true or false discoveries.

Scenario 3 examines what social psychology would look like today, if social psychologists had listened to Cohen. The scenario is the same as in the second scenario, including publication bias. There are 50% false hypotheses and 50% true hypotheses with an effect size of d = .4. The only difference is that researchers used N = 200 to test their hypotheses to achieve 80% power.

With 80% power, we need 470 tests (compared to 1,428 in Scenario 2) to produce 200 significant results, 235*.80 + 235*.05 = 188 + 12 = 200. Thus, the EDR is 200/470 = 43%. The true false discovery rate is 6%. The expected replication rate is 188*.80 + 12*.05 = 76%. Thus, we see that higher power increases replicability from 20% to 76% and lowers the false discovery rate from 18% to 6%.

Figure 3 shows the z-curve plot. Visual inspection shows that Figure 3 looks very different from Figures 1 and 2. The estimates are also different. In this example, sampling error inflated the EDR to be 58%, but the 95%CI includes the true value of 46%. The 95%CI does not include the ODR. Thus, there is evidence for publication bias, which is also visible by the steep drop in the distribution at 1.96.

Even with a low EDR of 20%, the maximum FDR is only 21%. Thus, we can conclude with confidence that at least 79% of the significant results are true positives. Remember, in the previous scenario, we could not rule out that most results are false positives. Moreover, the estimated replication rate is 73%, which underestimates the true replication rate of 76%, but the 95%CI includes the true value, 95%CI = 61% – 84%. Thus, if these studies were replicated, we would have a high success rate for actual replication studies.

Just imagine for a moment what social psychology might look like in a parallel universe where social psychologists followed Cohen’s advice. Why didn’t they? The reason is that they did not have z-curve. All they had was p < .05, and using p < .05, all three scenarios are identical. All three scenarios produced 200 significant results. Moreover, as Finkel et al. (2015) pointed out, smaller samples produce 200 significant results quicker than large samples. An additional advantage of small samples is that they inflate point estimates of the population effect size. Thus, the social psychologists with the smallest samples could brag about the biggest (illusory) effect sizes as long as nobody was able to publish replication studies with larger samples that deflated effect sizes of d = .8 to d = .08 (Joy-Gaba & Nosek, 2010).

This game is over, but social psychology – and other social sciences – have published thousands of significant p-values, and nobody knows whether they were obtained using scenario 1, 2, or 3, or probably a combination of these. This is where z-curve can make a difference. P-values are no longer equal when they are considered as a data point from a p-value distribution. In scenario 1, a p-value of .01 and even a p-value of .001 has no meaning. In contrast, in scenario 3 even a p-value of .02 is meaningful and more likely to reflect a true positive than a false positive result. This means that we can use z-curve analyses of published p-values to distinguish between probably false and probably true positives.

I illustrate this with three concrete examples from a project that examined the p-value distributions of over 200 social psychologists (Schimmack, in preparation). The first example has the lowest EDR in the sample. The EDR is 11% and because there are only 210 tests, the 95%CI is wide and includes 5%.

The maximum EDR estimate is high with 41% and the 95%CI includes 100%. This suggests that we cannot rule out the hypothesis that most significant results are false positives. However, the replication rate is 57% and the 95%CI, 45% to 69%, does not include 5%. Thus, some tests tested true hypotheses, but we do not know which ones.

Visual inspection of the plot shows a different distribution than Figure 2. There are more just significant p-values, z = 2.0 to 2.2 and more large z-scores (z > 4). This shows more heterogeneity in power. A comparison of the ODR with the EDR shows that the ODR falls outside the 95%CI of the EDR. This is evidence of publication bias or the use of questionable research practices. One solution to the presence of publication bias is to lower the criterion for statistical significance. As a result, the large number of just significant results is no longer significant and the ODR decreases. This is a post-hoc correction for publication bias. For example, we can lower alpha to .005.

As expected, the ODR decreases considerably from 70% to 39%. In contrast, the EDR increases. The reason is that many questionable research practices produce a pile of just significant p-values. As these values are no longer used to fit the z-curve, it predicts a lot fewer non-significant p-values. The model now underestimates p-values between 2 and 2.2. However, these values do not seem to come from a sampling distribution. Rather they stick out like a tower. By excluding them, the p-values that are still significant with alpha = .005 look more credible. Thus, we can correct for the use of QRPs by lowering alpha and by examining whether these p-values produced interesting discoveries. At the same time, we can ignore the p-values between .05 and .005 and await replication studies to provide empirical evidence whether these hypotheses receive empirical support.

The second example was picked because it was close to the median EDR (33) and ERR (66) in the sample of 200 social psychologists.

The larger sample of tests (k = 1,529) helps to obtain more precise estimates. A comparison of the ODR, 76%, and the 95%CI of the EDR, 12% to 48%, shows that publication bias is present. However, with an EDR of 33%, the maximum FDR is only 11% and the upper limit of the 95%CI is 39%. Thus, we can conclude with confidence that fewer than 50% of the significant results are false positives, however numerous findings might be false positives. Only replication studies can provide this information.

In this example, lowering alpha to .005 did not align the ODR and the EDR. This suggests that these values come from a sampling distribution where non-significant results were not published. Thus, adjusting the there is no simple fix to adjust the significance criterion. In this situation, we can conclude that the published p-values are unlikely to be false positives, but that replication studies are needed to ensure that published significant results are not false positives.

The third example is the social psychologists with the highest EDR. In this case, the EDR is actually a little bit lower than the ODR, suggesting that there is no publication bias. The high EDR also means that the maximum FDR is very small and even the upper limit of the 95%CI is only 7%.

Another advantage of data without publication bias is that it is not necessary to exclude non-significant results from the analysis. Fitting the model to all p-values produces much tighter estimates of the EDR and the maximum FDR.

The upper limit of the 95%CI for the FDR is now 4%. Thus, we conclude that no more than 5% of the p-values less than .05 are false positives. Even p = .02 is unlikely to be a false positive. Finally, the estimated replication rate is 84% with a tight confidence interval ranging from 78% to 90%. Thus, most of the published p-values are expected to replicate in an exact replication study.

I hope these examples make it clear how useful it can be to evaluate single p-values with prior information about the p-values distribution of a lab. As labs differ in their research practices, significant p-values are also different. Only if we ignore the research context and focus on a single result p = .02 equals p = .02. But once we see the broader distribution, p-values of .02 can provide stronger evidence against the null-hypothesis than p-values of .002.


Cohen tried and failed to change the research culture of social psychologists. Meta-psychological articles have puzzled why meta-analyses of power failed to increase power (Maxwell, 2004; Schimmack, 2012; Sedelmeier & Gigerenzer, 1989). Finkel et al. (2015) provided an explanation. In a game where the winner publishes as many significant results as possible, the optimal strategy is to conduct as many studies as possible with low power. This strategy continues to be rewarded in psychology, where jobs, promotions, grants, and pay raises are based on the number of publications. Cohen (1990) said less is more, but that is not true in a science that does not self-correct and treats every p-value less than .05 as a discovery.

To improve psychology as a science, we need to change the incentive structure and author-wise z-curve analyses can do this. Rather than using p < .05 (or p < .005) as a general rule to claim discoveries, claims of discoveries can be adjusted to the research practices of a researchers. As demonstrated here, this will reward researchers who follow Cohen’s rules and punish those who use questionable practices to produce p-values less than .05 (or Bayes-Factors > 3) without evidential value. And maybe, there is a badge for credible p-values one day.

(incomplete) References

Richard, F. D., Bond, C. F., Jr., & Stokes-Zoota, J. J. (2003). One hundred years of social psychology quantitatively described. Review of General Psychology, 7, 331–363.

The Replicability Index Is the Most Powerful Tool to Detect Publication Bias in Meta-Analyses


Methods for the detection of publication bias in meta-analyses were first introduced in the 1980s (Light & Pillemer, 1984). However, existing methods tend to have low statistical power to detect bias, especially when population effect sizes are heterogeneous (Renkewitz & Keiner, 2019). Here I show that the Replicability Index (RI) is a powerful method to detect selection for significance while controlling the type-I error risk better than the Test of Excessive Significance (TES). Unlike funnel plots and other regression methods, RI can be used without variation in sampling error across studies. Thus, it should be a default method to examine whether effect size estimates in a meta-analysis are inflated by selection for significance. However, the RI should not be used to correct effect size estimates. A significant results merely indicates that traditional effect size estimates are inflated by selection for significance or other questionable research practices that inflate the percentage of significant results.

Evaluating the Power and Type-I Error Rate of Bias Detection Methods

Just before the end of the year, and decade, Frank Renkewitz and Melanie Keiner published an important article that evaluated the performance of six bias detection methods in meta-analyses (Renkewitz & Keiner, 2019).

The article makes several important points.

1. Bias can distort effect size estimates in meta-analyses, but the amount of bias is sometimes trivial. Thus, bias detection is most important in conditions where effect sizes are inflated to a notable degree (say more than one-tenth of a standard deviation, e.g., from d = .2 to d = .3).

2. Several bias detection tools work well when studies are homogeneous (i.e. ,the population effect sizes are very similar). However, bias detection is more difficult when effect sizes are heterogeneous.

3. The most promising tool for heterogeneous data was the Test of Excessive Significance (Francis, 2013; Ioannidis, & Trikalinos, 2013). However, simulations without bias showed that the higher power of TES was achieved by a higher false-positive rate that exceeded the nominal level. The reason is that TES relies on the assumption that all studies have the same population effect size and this assumption is violated when population effect sizes are heterogeneous.

This blog post examines two new methods to detect publication bias and compares them to the TES and the Test of Insufficient Variance (TIVA) that performed well when effect sizes were homogeneous (Renkewitz & Keiner , 2019). These methods are not entirely new. One method is the Incredibility Index, which is similar to TES (Schimmack, 2012). The second method is the Replicability Index, which corrects estimates of observed power for inflation when bias is present.

The Basic Logic of Power-Based Bias Tests

The mathematical foundations for bias tests based on statistical power were introduced by Sterling et al. (1995). Statistical power is defined as the conditional probability of obtaining a significant result when the null-hypothesis is false. When the null-hypothesis is true, the probability of obtaining a significant result is set by the criterion for a type-I error, alpha. To simplify, we can treat cases where the null-hypothesis is true as the boundary value for power (Brunner & Schimmack, 2019). I call this unconditional power. Sterling et al. (1995) pointed out that for studies with heterogeneity in sample sizes, effect sizes or both, the discoery rate; that is the percentage of significant results, is predicted by the mean unconditional power of studies. This insight makes it possible to detect bias by comparing the observed discovery rate (the percentage of significant results) to the expected discovery rate based on the unconditional power of studies. The empirical challenge is to obtain useful estimates of unconditional mean power, which depends on the unknown population effect sizes.

Ioannidis and Trialinos (2007) were the first to propose a bias test that relied on a comparison of expected and observed discovery rates. The method is called Test of Excessive Significance (TES). They proposed a conventional meta-analysis of effect sizes to obtain an estimate of the population effect size, and then to use this effect size and information about sample sizes to compute power of individual studies. The final step was to compare the expected discovery rate (e.g., 5 out of 10 studies) with the observed discovery rate (8 out of 10 studies) with a chi-square test and to test the null-hypothesis of no bias with alpha = .10. They did point out that TES is biased when effect sizes are heterogeneous (see Renkewitz & Keiner, 2019, for a detailed discussion).

Schimmack (2012) proposed an alternative approach that does not assume a fixed effect sizes across studies, called the incredibility index. The first step is to compute observed-power for each study. The second step is to compute the average of these observed power estimates. This average effect size is then used as an estimate of the mean unconditional power. The final step is to compute the binomial probability of obtaining as many or more significant results that were observed for the estimated unconditional power. Schimmack (2012) showed that this approach avoids some of the problems of TES when effect sizes are heterogeneous. Thus, it is likely that the Incredibility Index produces fewer false positives than TES.

Like TES, the incredibility index has low power to detect bias because bias inflates observed power. Thus, the expected discovery rate is inflated, which makes it a conservative test of bias. Schimmack (2016) proposed a solution to this problem. As the inflation in the expected discovery rate is correlated with the amount of bias, the discrepancy between the observed and expected discovery rate indexes inflation. Thus, it is possible to correct the estimated discovery rate by the amount of observed inflation. For example, if the expected discovery rate is 70% and the observed discovery rate is 90%, the inflation is 20 percentage points. This inflation can be deducted from the expected discovery rate to get a less biased estimate of the unconditional mean power. In this example, this would be 70% – 20% = 50%. This inflation-adjusted estimate is called the Replicability Index. Although the Replicability Index risks a higher type-I error rate than the Incredibility Index, it may be more powerful and have a better type-I error control than TES.

To test these hypotheses, I conducted some simulation studies that compared the performance of four bias detection methods. The Test of Insufficient Variance (TIVA; Schimmack, 2015) was included because it has good power with homogeneous data (Renkewitz & Keiner, 2019). The other three tests were TES, ICI, and RI.

Selection bias was simulated with probabilities of 0, .1, .2, and 1. A selection probability of 0 implies that non-significant results are never published. A selection probability of .1 implies that there is a 10% chance that a non-significant result is published when it is observed. Finally, a selection probability of 1 implies that there is no bias and all non-significant results are published.

Effect sizes varied from 0 to .6. Heterogeneity was simulated with a normal distribution with SDs ranging from 0 to .6. Sample sizes were simulated by drawing from a uniform distribution with values between 20 and 40, 100, and 200 as maximum. The number of studies in a meta-analysis were 5, 10, 20, and 30. The focus was on small sets of studies because power to detect bias increases with the number of studies and power was often close to 100% with k = 30.

Each condition was simulated 100 times and the percentage of significant results with alpha = .10 (one-tailed) was used to compute power and type-I error rates.



Figure 1 shows a plot of the mean observed d-scores as a function of the mean population d-scores. In situations without heterogeneity, mean population d-scores corresponded to the simulated values of d = 0 to d = .6. However, with heterogeneity, mean population d-scores varied due to sampling from the normal distribution of population effect sizes.

The figure shows that bias could be negative or positive, but that overestimation is much more common than underestimation.  Underestimation was most likely when the population effect size was 0, there was no variability (SD = 0), and there was no selection for significance.  With complete selection for significance, bias always overestimated population effect sizes, because selection was simulated to be one-sided. The reason is that meta-analysis rarely show many significant results in both directions.  

An Analysis of Variance (ANOVA) with number of studies (k), mean population effect size (mpd), heterogeneity of population effect sizes (SD), range of sample sizes (Nmax) and selection bias (sel.bias) showed a four-way interaction, t = 3.70.   This four-way interaction qualified main effects that showed bias decreases with effect sizes (d), heterogeneity (SD), range of sample sizes (N), and increased with severity of selection bias (sel.bias).  

The effect of selection bias is obvious in that effect size estimates are unbiased when there is no selection bias and increases with severity of selection bias.  Figure 2 illustrates the three way interaction for the remaining factors with the most extreme selection bias; that is, all non-significant results are suppressed. 

The most dramatic inflation of effect sizes occurs when sample sizes are small (N = 20-40), the mean population effect size is zero, and there is no heterogeneity (light blue bars). This condition simulates a meta-analysis where the null-hypothesis is true. Inflation is reduced, but still considerable (d = .42), when the population effect is large (d = .6). Heterogeneity reduces bias because it increases the mean population effect size. However, even with d = .6 and heterogeneity, small samples continue to produce inflated estimates by d = .25 (dark red). Increasing sample sizes (N = 20 to 200) reduces inflation considerably. With d = 0 and SD = 0, inflation is still considerable, d = .52, but all other conditions have negligible amounts of inflation, d < .10.

As sample sizes are known, they provide some valuable information about the presence of bias in a meta-analysis. If studies with large samples are available, it is reasonable to limit a meta-analysis to the larger and more trustworthy studies (Stanley, Jarrell, & Doucouliagos, 2010).

Discovery Rates

If all results are published, there is no selection bias and effect size estimates are unbiased. When studies are selected for significance, the amount of bias is a function of the amount of studies with non-significant results that are suppressed. When all non-significant results are suppressed, the amount of selection bias depends on the mean power of the studies before selection for significance which is reflected in the discovery rate (i.e., the percentage of studies with significant results). Figure 3 shows the discovery rates for the same conditions that were used in Figure 2. The lowest discovery rate exists when the null-hypothesis is true. In this case, only 2.5% of studies produce significant results that are published. The percentage is 2.5% and not 5% because selection also takes the direction of the effect into account. Smaller sample sizes (left side) have lower discovery rates than larger sample sizes (right side) because larger samples have more power to produce significant results. In addition, studies with larger effect sizes have higher discovery rates than studies with small effect sizes because larger effect sizes increase power. In addition, more variability in effect sizes increases power because variability increases the mean population effect sizes, which also increases power.

In conclusion, the amount of selection bias and the amount of inflation of effect sizes varies across conditions as a function of effect sizes, sample sizes, heterogeneity, and the severity of selection bias. The factorial design covers a wide range of conditions. A good bias detection method should have high power to detect bias across all conditions with selection bias and low type-I error rates across conditions without selection bias.

Overall Performance of Bias Detection Methods

Figure 4 shows the overall results for 235,200 simulations across a wide range of conditions. The results replicate Renkewitz and Keiner’s finding that TES produces more type-I errors than the other methods, although the average rate of type-I errors is below the nominal level of alpha = .10. The error rate of the incredibility index is practically zero, indicating that it is much more conservative than TES. The improvement for type-I errors does not come at the cost of lower power. TES and ICI have the same level of power. This finding shows that computing observed power for each individual study is superior than assuming a fixed effect size across studies. More important, the best performing method is the Replicability Index (RI), which has considerably more power because it corrects for inflation in observed power that is introduced by selection for significance. This is a promising results because one of the limitation of the bias tests examined by Renkewitz and Keiner was the low power to detect selection bias across a wide range of realistic scenarios.

Logistic regression analyses for power showed significant five-way interactions for TES, IC, and RI. For TIVA, two four-way interactions were significant. For type-I error rates no four-way interactions were significant, but at least one three-way interaction was significant. These results show that results systematic vary in a rather complex manner across the simulated conditions. The following results show the performance of the four methods in specific conditions.

Number of Studies (k)

Detection of bias is a function of the amount of bias and the number of studies. With small sets of studies (k = 5), it is difficult to detect power. In addition, low power can suppress false-positive rates because significant results without selection bias are even less likely than significant results with selection bias. Thus, it is important to examine the influence of the number of studies on power and false positive rates.

Figure 5 shows the results for power. TIVA does not gain much power with increasing sample sizes. The other three methods clearly become more powerful as sample sizes increase. However, only the R-Index shows good power with twenty studies and still acceptable studies with just 10 studies. The R-Index with 10 studies is as powerful as TES and ICI with 10 studies.

Figure 6 shows the results for the type-I error rates. Most important, the high power of the R-Index is not achieved by inflating type-I error rates, which are still well-below the nominal level of .10. A comparison of TES and ICI shows that ICI controls type-I error much better than TES. TES even exceeds the nominal level of .10 with 30 studies and this problem is going to increase as the number of studies gets larger.

Selection Rate

Renkewitz and Keiner noticed that power decreases when there is a small probability that non-significant results are published. To simplify the results for the amount of selection bias, I focused on the condition with n = 30 studies, which gives all methods the maximum power to detect selection bias. Figure 7 confirms that power to detect bias deteriorates when non-significant results are published. However, the influence of selection rate varies across methods. TIVA is only useful when only significant results are selected, but even TES and ICI have only modest power even if the probability of a non-significant result to be published is only 10%. Only the R-Index still has good power, and power is still higher with a 20% chance to select a non-significant result than with a 10% selection rate for TES and ICI.

Population Mean Effect Size

With complete selection bias (no significant results), power had ceiling effects. Thus, I used k = 10 to illustrate the effect of population effect sizes on power and type-I error rates. (Figure 8)

In general, power decreased as the population mean effect sizes increased. The reason is that there is less selection because the discovery rates are higher. Power decreased quickly to unacceptable levels (< 50%) for all methods except the R-Index. The R-Index maintained good power even with the maximum effect size of d = .6.

Figure 9 shows that the good power of the R-Index is not achieved by inflating type-I error rates. The type-I error rate is well below the nominal level of .10. In contrast, TES exceeds the nominal level with d = .6.

Variability in Population Effect Sizes

I next examined the influence of heterogeneity in population effect sizes on power and type-I error rates. The results in Figure 10 show that hetergeneity decreases power for all methods. However, the effect is much less sever for the RI than for the other methods. Even with maximum heterogeneity, it has good power to detect publication bias.

Figure 11 shows that the high power of RI is not achieved by inflating type-I error rates. The only method with a high error-rate is TES with high heterogeneity.

Variability in Sample Sizes

With a wider range of sample sizes, average power increases. And with higher power, the discovery rate increases and there is less selection for significance. This reduces power to detect selection for significance. This trend is visible in Figure 12. Even with sample sizes ranging from 20 to 100, TIVA, TES, and IC have modest power to detect bias. However, RI maintains good levels of power even when sample sizes range from 20 to 200.

Once more, only TES shows problems with the type-I error rate when heterogeneity is high (Figure 13). Thus, the high power of RI is not achieved by inflating type-I error rates.

Stress Test

The following analyses examined RI’s performance more closely. The effect of selection bias is self-evident. As more non-significant results are available, power to detect bias decreases. However, bias also decreases. Thus, I focus on the unfortunately still realistic scenario that only significant results are published. I focus on the scenario with the most heterogeneity in sample sizes (N = 20 to 200) because it has the lowest power to detect bias. I picked the lowest and highest levels of population effect sizes and variability to illustrate the effect of these factors on power and type-I error rates. I present results for all four set sizes.

The results for power show that with only 5 studies, bias can only be detected with good power if the null-hypothesis is true. Heterogeneity or large effect sizes produce unacceptably low power. This means that the use of bias tests for small sets of studies is lopsided. Positive results strongly indicate severe bias, but negative results are inconclusive. With 10 studies, power is acceptable for homogeneous and high effect sizes as well as for heterogeneous and low effect sizes, but not for high effect sizes and high heterogeneity. With 20 or more studies, power is good for all scenarios.

The results for the type-I error rates reveal one scenario with dramatically inflated type-I error rates, namely meta-analysis with a large population effect size and no heterogeneity in population effect sizes.


The high type-I error rate is limited to cases with high power. In this case, the inflation correction over-corrects. A solution to this problem is found by considering the fact that inflation is a non-linear function of power. With unconditional power of .05, selection for significance inflates observed power to .50, a 10 fold increase. However, power of .50 is inflated to .75, which is only a 50% increase. Thus, I modified the R-Index formula and made inflation contingent on the observed discovery rate.

RI2 = Mean.Observed.Power – (Observed Discovery Rate – Mean.Observed.Power)*(1-Observed.Discovery.Rate). This version of the R-Index reduces power, although power is still superior to the IC.

It also fixed the type-I error problem at least with sample sizes up to N = 30.

Example 1: Bem (2011)

Bem’s (2011) sensational and deeply flawed article triggered the replication crisis and the search for bias-detection tools (Francis, 2012; Schimmack, 2012). Table 1 shows that all tests indicate that Bem used questionable research practices to produce significant results in 9 out of 10 tests. This is confirmed by examination of his original data (Schimmack, 2018). For example, for one study, Bem combined results from four smaller samples with non-significant results into one sample with a significant result. The results also show that both versions of the Replicability Index are more powerful than the other tests.


Example 2: Francis (2014) Audit of Psychological Science

Francis audited multiple-study articles in the journal Psychological Science from 2009-2012. The main problem with the focus on single articles is that they often contain relatively few studies and the simulation studies showed that bias tests tend to have low power if 5 or fewer studies are available (Renkewitz & Keiner, 2019). Nevertheless, Francis found that 82% of the investigated articles showed signs of bias, p < .10. This finding seems very high given the low power of TES in the simulation studies. It would mean that selection bias in these articles was very high and power of the studies was extremely low and homogeneous, which provides the ideal conditions to detect bias. However, the high type-I error rates of TES under some conditions may have produced more false positive results than the nominal level of .10 suggests. Moreover, Francis (2014) modified TES in ways that may have further increased the risk of false positives. Thus, it is interesting to reexamine the 44 studies with other bias tests. Unlike Francis, I coded one focal hypothesis test per study.

I then applied the bias detection methods. Table 2 shows the p-values.

2012Anderson, Kraus, Galinsky, & Keltner0.1670.3880.1220.3870.1110.307
2012Bauer, Wilkie, Kim, & Bodenhausen0.0620.0040.0220.0880.0000.013
2012Birtel & Crisp0.1330.0700.0760.1930.0040.064
2012Converse & Fishbach0.1100.1300.1610.3190.0490.199
2012Converse, Risen, & Carter Karmic0.0430.0000.0220.0650.0000.010
2012Keysar, Hayakawa, &0.0910.1150.0670.1190.0030.043
2012Leung et al.0.0760.0470.0630.1190.0030.043
2012Rounding, Lee, Jacobson, & Ji0.0360.1580.0750.1520.0040.054
2012Savani & Rattan0.0640.0030.0280.0670.0000.017
2012van Boxtel & Koch0.0710.4960.7180.4980.2000.421
2011Evans, Horowitz, & Wolfe0.4260.9380.9860.6280.3790.606
2011Inesi, Botti, Dubois, Rucker, & Galinsky0.0260.0430.0610.1220.0030.045
2011Nordgren, Morris McDonnell, & Loewenstein0.0900.0260.1140.1960.0120.094
2011Savani, Stephens, & Markus0.0630.0270.0300.0800.0000.018
2011Todd, Hanko, Galinsky, & Mussweiler0.0430.0000.0240.0510.0000.005
2011Tuk, Trampe, & Warlop0.0920.0000.0280.0970.0000.017
2010Balcetis & Dunning0.0760.1130.0920.1260.0030.048
2010Bowles & Gelfand0.0570.5940.2080.2810.0430.183
2010Damisch, Stoberock, & Mussweiler0.0570.0000.0170.0730.0000.007
2010de Hevia & Spelke0.0700.3510.2100.3410.0620.224
2010Ersner-Hershfield, Galinsky, Kray, & King0.0730.0040.0050.0890.0000.013
2010Gao, McCarthy, & Scholl0.1150.1410.1890.3610.0410.195
2010Lammers, Stapel, & Galinsky0.0240.0220.1130.0610.0010.021
2010Li, Wei, & Soman0.0790.0300.1370.2310.0220.129
2010Maddux et al.0.0140.3440.1000.1890.0100.087
2010McGraw & Warren0.0810.9930.3020.1480.0060.066
2010Sackett, Meyvis, Nelson, Converse, & Sackett0.0330.0020.0250.0480.0000.011
2010Savani, Markus, Naidu, Kumar, & Berlia0.0580.0110.0090.0620.0000.014
2010Senay, Albarracín, & Noguchi0.0900.0000.0170.0810.0000.010
2010West, Anderson, Bedwell, & Pratt0.1570.2230.2260.2870.0320.160
2009Alter & Oppenheimer0.0710.0000.0410.0530.0000.006
2009Ashton-James, Maddux, Galinsky, & Chartrand0.0350.1750.1330.2700.0250.142
2009Fast & Chen0.0720.0060.0360.0730.0000.014
2009Fast, Gruenfeld, Sivanathan, & Galinsky0.0690.0080.0420.1180.0010.030
2009Garcia & Tor0.0891.0000.4220.1900.0190.117
2009González & McLennan0.1390.0800.1940.3030.0550.208
2009Hahn, Close, & Graf0.3480.0680.2860.4740.1750.390
2009Hart & Albarracín0.0350.0010.0480.0930.0000.015
2009Janssen & Caramazza0.0830.0510.3100.3920.1150.313
2009Jostmann, Lakens, & Schubert0.0900.0000.0260.0980.0000.018
2009Labroo, Lambotte, & Zhang0.0080.0540.0710.1480.0030.051
2009Nordgren, van Harreveld, & van der Pligt0.1000.0140.0510.1350.0020.041
2009Wakslak & Trope0.0610.0080.0290.0650.0000.010
2009Zhou, Vohs, & Baumeister0.0410.0090.0430.0970.0020.036

The Figure shows the percentage of significant results for the various methods. The results confirm that despite the small number of studies, the majority of multiple-study articles show significant evidence of bias. Although statistical significance does not speak directly to effect sizes, the fact that these tests were significant with a small set of studies implies that the amount of bias is large. This is also confirmed by a z-curve analysis that provides an estimate of the average bias across all studies (Schimmack, 2019).

A comparison of the methods shows with real data that the R-Index (RI1) is the most powerful method and even more powerful than Francis’s method that used multiple studies from a single study. The good performance of TIVA shows that population effect sizes are rather homogeneous as TIVA has low power with heterogeneous data. The Incredibility Index has the worst performance because it has an ultra-conservative type-I error rate. The most important finding is that the R-Index can be used with small sets of studies to demonstrate moderate to large bias.


In 2012, I introduced the Incredibility Index as a statistical tool to reveal selection bias; that is, the published results were selected for significance from a larger number of results. I compared the IC with TES and pointed out some advantages of averaging power rather than effect sizes. However, I did not present extensive simulation studies to compare the performance of the two tests. In 2014, I introduced the replicability index to predict the outcome of replication studies. The replicability index corrects for the inflation of observed power when selection for significance is present. I did not think about RI as a bias test. However, Renkewitz and Keiner (2019) demonstrated that TES has low power and inflated type-I error rates. Here I examined whether IC performed better than TES and I found it did. Most important, it has much more conservative type-I error rates even with extreme heterogeneity. The reason is that selection for significance inflates observed power which is used to compute the expected percentage of significant results. This led me to see whether the bias correction that is used to compute the Replicability Index can boost power, while maintaining acceptable type-I error rates. The present results shows that this is the case for a wide range of scenarios. The only exception are meta-analysis of studies with a high population effect size and low heterogeneity in effect sizes. To avoid this problem, I created an alternative R-Index that reduces the inflation adjustment as a function of the percentage of non-significant results that are reported. I showed that the R-Index is a powerful tool that detects bias in Bem’s (2011) article and in a large number of multiple-study articles published in Psychological Science. In conclusion, the replicability index is the most powerful test for the presence of selection bias and it should be routinely used in meta-analyses to ensure that effect sizes estimates are not inflated by selective publishing of significant results. As the use of questionable practices is no longer acceptable, the R-Index can be used by editors to triage manuscripts with questionable results or to ask for a new, pre-registered, well-powered additional study. The R-Index can also be used in tenure and promotion evaluations to reward researchers that publish credible results that are likely to replicate.


Francis, G. (2013). Replication, statistical consistency, and publication bias. Journal of Mathematical Psychology, 57, 153–169.

Ioannidis, J. P. A., & Trikalinos, T. A. (2007). An exploratory test for an excess of significant findings. Clinical Trials: Journal of the Society for Clinical Trials, 4, 245–253.

 R. J. Light; D. B. Pillemer (1984). Summing up: The Science of Reviewing Research. Cambridge, Massachusetts: Harvard University Press.

Renkewitz, F., & Keiner, M. (2019). How to Detect Publication Bias in Psychological Research
A Comparative Evaluation of Six Statistical Methods. Zeitschrift für Psychologie, 227, 261-279.

Schimmack, U. (2012). The ironic effect of significant results on the credibility of multiple-study articles. Psychological Methods, 17, 551–566. doi:10.1037/a0029487

Schimmack, U. (2014, December 30). The test of insufficient variance (TIVA): A new tool for the detection of questionable research practices [Blog Post]. Retrieved from

Schimmack, U. (2016). A revised introduction to the R-Index. Retrieved

Sterling, T. D., Rosenbaum, W. L., & Weinkam, J. J. (1995). Publication decisions revisited: The effect of the outcome of statistical tests on the decision to publish and vice versa. The American Statistician, 49, 108–112.

An Introduction to Z-Curve: A method for estimating mean power after selection for significance (replicability)

UPDATE 5/13/2019   Our manuscript on the z-curve method for estimation of mean power after selection for significance has been accepted for publication in Meta-Psychology. As estimation of actual power is an important tool for meta-psychologists, we are happy that z-curve found its home in Meta-Psychology.  We also enjoyed the open and constructive review process at Meta-Psychology.  Definitely will try Meta-Psychology again for future work (look out for z-curve.2.0 with many new features).


Since 2015, Jerry Brunner and I have been working on a statistical tool that can estimate mean (statitical) power for a set of studies with heterogeneous sample sizes and effect sizes (heterogeneity in non-centrality parameters and true power).   This method corrects for the inflation in mean observed power that is introduced by the selection for statistical significance.   Knowledge about mean power makes it possible to predict the success rate of exact replication studies.   For example, if a set of studies with mean power of 60% were replicated exactly (including sample sizes), we would expect that 60% of the replication studies produce a significant result again.

Our latest manuscript is a revision of an earlier manuscript that received a revise and resubmit decision from the free, open-peer-review journal Meta-Psychology.  We consider it the most authoritative introduction to z-curve that should be used to learn about z-curve, critic z-curve, or as a citation for studies that use z-curve.

Cite as “submitted for publication”.

Final.Revision.874-Manuscript in PDF-2236-1-4-20180425 mva final (002)

Feel free to ask questions, provide comments, and critic our manuscript in the comments section.  We are proud to be an open science lab, and consider criticism an opportunity to improve z-curve and our understanding of power estimation.

Latest R-Code to run Z.Curve (Z.Curve.Public.18.10.28).
[updated 18/11/17]   [35 lines of code]
call function  mean.power = zcurve(pvalues,Plot=FALSE,alpha=.05,bw=.05)[1]

Z-Curve related Talks
Presentation on Z-curve and application to BS Experimental Social Psychology and (Mostly) WS-Cognitive Psychology at U Waterloo (November 2, 2018)
[Powerpoint Slides]

Visual Inspection of Strength of Evidence: P-Curve vs. Z-Curve

Statistics courses often introduce students to a bewildering range of statistical test.  They rarely point out how test statistics are related.  For example, although t-tests may be easier to understand than F-tests, every t-test could be performed as an F-test and the F-value in the F-test is simply the square of the t-value (t^2 or t*t).

At an even more conceptual level, all test statistics are ratios of the effect size (ES) and the amount of sampling error (ES).   The ratio is sometimes called the signal (ES) to noise (ES) ratio.  The higher the signal to noise ratio (ES/SE), the stronger the observed results deviate from the hypothesis that the effect size is zero.  This hypothesis is often called the null-hypothesis, but this terminology has created some confusing.  It is also sometimes called the nil-hypothesis the zero-effect hypothesis or the no-effect hypothesis.  Most important, the test-statistic is expected to average zero if the same experiment could be replicated a gazillion times.

The test statistics of statistical tests cannot be directly compared.  A t-value of 2 in a study with N = 10 participants provides weaker evidence against the null-hypothesis than a z-score of 1.96.  and an F-value of 4 with df(1,40) provides weaker evidence than an F(10,200) = 4 result.  It is only possible to compare test values directly that have the same sampling distribution (z with z, F(1,40) with F(1,40), etc.).

There are three solutions to this problem. One solution is to use effect sizes as the unit of analysis. This is useful if the aim is effect size estimation.  Effect size estimation has become the dominant approach in meta-analysis.  This blog post is not about effect size estimation.  I just mention it because many readers may be familiar with effect size meta-analysis, but not familiar with meta-analysis of test statistics that reflect the ratio of effect size and sampling error (Effect size meta-analysis: unit = ES; Test Statistic Meta-Analysis: unit ES/SE).


There are two approaches to standardize test statistics so that they have a common unit of measurement.  The first approach goes back to Ronald Fisher, who is considered the founder of modern statistics for researchers.  Following Fisher it is common practice to convert test-statistics into p-values (for this blog post assumes that you are familiar with p-values).   P-values have the same meaning independent of the test statistic that was used to compute them.   That is, p = .05 based on a z-test, t-test, or an F-test provide equally strong evidence against the null-hypothesis (Bayesians disagree, but that is a different story).   The use of p-values as a common metric to examine strength of evidence (evidential value) was largely forgotten, until Simonsohn, Simmons, and Nelson (SSN) used p-values to develop a statistical tool that takes publication bias and questionable research practices into account.  This statistical approach is called p-curve.  P-curve is a family of statistical methods.  This post is about the p-curve plot.

A p-curve plot is essentially a histogram of p-values with two characteristics. First, it only shows significant p-values (p < .05, two-tailed).  Second, it plots the p-values between 0 and .05 with 5 bars.  The Figure shows a p-curve for Motyl et al.’s (2017) focal hypothesis tests in social psychology.  I only selected t-test and F-tests from studies with between-subject manipulations.


The main purpose of a p-curve plot is to examine whether the distribution of p-values is uniform (all bars have the same height).  It is evident that the distribution for Motyl et al.’s data is not uniform.  Most of the p-values fall into the lowest range between 0 and .01. This pattern is called “rigth-skewed.”  A right-skewed plot shows that the set of studies has evidential value. That is, some test statistics are based on non-zero effect sizes.  The taller the bar on the left is, the greater the proportion of studies with an effect.  Importantly, meta-analyses of p-values do not provide information about effect sizes because p-values take effect size and sampling error into account.

The main inference that can be drawn from a visual inspection of a p-curve plot is how unlikely it is that all significant results are false positives; that is, the p-value is below .05 (statistically significant), but this strong deviation from 0 was entirely due to sampling error, while the true effect size is 0.

The next Figure also shows a plot of p-values.  The difference is that it shows the full range of p-values and that it differentiates more between p-values because p = .09 provides weaker evidence than p = .0009.


The histogram shows that most p-values are below p < .001.  It also shows very few non-significant results.  However, this plot is not more informative than the actual p-curve plot. The only conclusion that is readily visible is that the distribution is not uniform.

The main problem with p-value plots is that p-values do not have interval scale properties.  This means, the difference between p = .4 and p = .3 is not the same as the difference between p = .10 and p = .00 (e.g., .001).


Stouffer developed an alternative method to Fisher’s p-value meta-analysis.  Every p-value can be transformed into a z-scores that corresponds to a particular p-value.  It is important to distinguish between one-sided and two-sided p-values.  The transformation requires the use of one-sided p-values, which can be obtained by simply dividing a two-sided p-value by 2.  A z-score of -1.96 corresponds to a one-sided p-value of 0.025 and a z-score of 1.96 corresponds to a one-sided p-values of 0.025.  In a two sided test, the sign no longer matters and the two p-values are added to yield 0.025 + 0.025 = 0.05.

In a standard meta-analysis, we would want to use one-sided p-values to maintain information about the sign.  However, if the set of studies examines different hypothesis (as in Motyl et al.’s analysis of social psychology in general) the sign is no longer important.   So, the transformed two-sided p-values produce absolute (only positive) z-scores.

The formula in R is Z = -qnorm(p/2)   [p = two.sided p-value]

For very strong evidence this formula creates problems. that can be solved by using the log.P=TRUE option in R.

Z = -qnorm(log(p/2), log.p=TRUE)

The plot shows the relationship between z-scores and p-values.  While z-scores are relatively insensitive to variation in p-values from .05 to 1, p-values are relatively insensitive to variation in z-scores from 2 to 15.

The next figure shows the relationship only for significant p-values.  Limiting the distribution of p-values does not change the fact that p-values and z-values have very different distributions and a non-linear relationship.

The advantage of using (absolute) z-scores is that z-scores have ratio scale properties.  A z-score of zero has real meaning and corresponds to the absence of evidence for an effect; the observed effect size is 0.  A z-score of 2 is twice as strong as a z-score of 1. For example, given the same sampling error the effect size for a z-score of 2 is twice as large as the effect size for a z-score of 1 (e.g., d = .2, se = .2, z = d/se = 1,  d = 4, se = .2, d/se = 2).

It is possible to create the typical p-curve plot with z-scores by selecting only z-scores above z = 1.96. However, this graph is not informative because the null-hypothesis does not predict a uniform distribution of z-scores.   For z-values the central tendency of z-values is more important.  When the null-hypothesis is true, p-values have a uniform distribution and we would expect an equal number of p-values between 0 and 0.025 and between 0.025 and 0.050.   A two-sided p-value of .025 corresponds to a one-sided p-value of 0.0125 and the corresponding z-value is 2.24

p = .025
[1] 2.241403

Thus, the analog to a p-value plot is to examine how many significant z-scores fall into the region from 1.96 to 2.24 versus the region with z-values greater than 2.24.


The histogram of z-values is called z-curve.  The plot shows that most z-values are in the range between 1 and 6, but the histogram stretches out to 20 because a few studies had very high z-values.  The red line shows z = 1.96. All values on the left are not significant with alpha = .05 and all values on the right are significant (p < .05).  The dotted blue line corresponds to p = .025 (two tailed).  Clearly there are more z-scores above 2.24 than between 1.96 and 2.24.  Thus, a z-curve plot provides the same information as a p-curve plot.  The distribution of z-scores suggests that some significant results reflect true effects.

However, a z-curve plot provides a lot of additional information.  The next plot removes the long tail of rare results with extreme evidence and limits the plot to z-scores in the range between 0 and 6.  A z-score of six implies a signal to noise ratio of 6:1 and corresponds to a p-value of p = 0.000000002 or 1 out of 2,027,189,384 (~ 2 billion) events. Even particle physics settle for z = 5 to decide that an effect was observed if it is so unlikely for a test result to occur by chance.

> pnorm(-6)*2
[1] 1.973175e-09

Another addition to the plot is to include a line that identifies z-scores between 1.65 and 1.96.  These z-scores correspond to two-sided p-values between .05 and .10. These values are often published as weak but sufficient evidence to support the inference that a (predicted) effect was detected. These z-scores also correspond to p-values below .05 in one-sided tests.


A major advantage of z-scores over p-values is that p-values are conditional probabilities based on the assumption that the null-hypothesis is true, but this hypothesis can be safely rejected with these data.  So, the actual p-values are not important because they are conditional on a hypothesis that we know to be false.   It is like saying, I would be a giant if everybody else were 1 foot tall (like Gulliver in Lilliput), but everybody else is not 1 foot tall and I am not a giant.

Z-scores are not conditioned on any hypothesis. They simply show the ratio of the observed effect size and sampling error.  Moreover, the distribution of z-scores tell us something about the ratio of the true effect sizes and sampling error.  The reason is that sampling error is random and like any random variable has a mean of zero.  Therefore, the mode, median, or mean of a z-curve plot tells us something about ratio of the true effect sizes and sampling error.  The more the center of a distribution is shifted to the right, the stronger is the evidence against the null-hypothesis.  In a p-curve plot, this is reflected in the height of the bar with p-values below .01 (z > 2.58), but a z-curve plot shows the actual distribution of the strength of evidence and makes it possible to see where the center of a distribution is (without more rigorous statistical analyses of the data).

For example, in the plot above it is not difficult to see the mode (peak) of the distribution.  The most common z-values are between 2 and 2.2, which corresponds to p-values of .046 (pnorm(-2.2)*2) and .028 (pnorm(-2.2)*2).   This suggests that the modal study has a ratio of 2:1 for effect size over sampling error.

The distribution of z-values does not look like a normal distribution. One explanation for this is that studies vary in sampling errors and population effect sizes.  Another explanation is that the set of studies is not a representative sample of all studies that were conducted.   It is possible to test this prediction by trying to fit a simple model to the data that assumes representative sampling of studies (no selection bias or p-hacking) and that assumes that all studies have the same ratio of population effect size over sampling error.   The median z-score provides an estimate of the center of the sampling distribution.  The median for these data is z = 2.56.   The next picture shows the predicted sampling distribution of this model, which is an approximately normal distribution with a folded tail.



A comparison of the observed and predicted distribution of z-values shows some discrepancies. Most important is that there are too few non-significant results.  This observation provides evidence that the results are not a representative sample of studies.  Either non-significant results were not reported or questionable research practices were used to produce significant results by increasing the type-I error rate without reporting this (e.g., multiple testing of several DVs, or repeated checking for significance during the course of a study).

It is important to see the difference between the philosophies of p-curve and z-curve. p-curve assumes that non-significant results provide no credible evidence and discards these results if they are reported.  Z-curve first checks whether non-significant results are missing.  In this way, p-curve is not a suitable tool for assessing publication bias or other problems, whereas even a simple visual inspection of z-curve plots provides information about publication bias and questionable research practices.


The next graph shows a model that selects for significance.  It no longer attempts to match the distribution of non-significant results.  The objective is only to match the distribution of significant z-values.  You can do this by hand and simply try out different values for the center of the normal distribution.  The lower the center, the more z-scores are missing because they are not significant.  As a result, the density of the predicted curve needs to be adjusted to reflect the fact that some of the area is missing.

center.z = 1.8  #pick a value
z = seq(0,6,.001)  #create the range of z-values
y = dnorm(z,center.z,1) + dnorm(z,-center.z,1)  # get the density for a folded normal
y2 = y #duplicate densities
y2[x < 1.96] = 0   # simulate selection bias, density for non-significant results is zero
scale = sum(y2)/sum(y)  # get the scaling factor so that area under the curve of only significant results is 1.
y = y / scale   # adjust the densities accordingly

# draw a histogram of z-values
# input is  z.val.input
# example; z.val.input = rnorm(1000,2)
hist(z.val.input,freq=FALSE,xlim=c(0,6),ylim=c(0,1),breaks=seq(0,20,.2), xlab=””,ylab=”Density”,main=”Z-Curve”)

abline(v=1.96,col=”red”)   # draw the line for alpha = .05 (two-tailed)
abline(v=1.65,col=”red”,lty=2)  # draw marginal significance (alpha = .10 (two-tailed)

par(new=TRUE) #command to superimpose next plot on histogram

# draw the predicted sampling distribution
plot(x,y,type=”l”,lwd=4,ylim=c(0,1),xlim=c(0,6),xlab=”(absolute) z-values”,ylab=””)

Although this model fits the data better than the previous model without selection bias, it still has problems fitting the data.  The reason is that there is substantial heterogeneity in the true strength of evidence.  In other words, the variability in z-scores is not just sampling error but also variability in sampling errors (some studies have larger samples than others) and population effect sizes (some studies examine weak effects and others examine strong effects).

Jerry Brunner and I developed a mixture model to fit a predicted model to the observed distribution of z-values.  In a nutshell the mixture model has multiple (folded) normal distributions.  Jerry’s z-curve lets the center of the normal distribution move around and give different weights to them.  Uli’s z-curve uses fixed centers one standard deviation apart (0,1,2,3,4,5 & 6) and uses different weights to fit the model to the data.  Simulation studies show that both methods work well.  Jerry’s method works a bit better if there is little variability and Uli’s method works a bit better with large variability.

The next figure shows the result for Uli’s method because the data have large variability.


The dark blue line in the figure shows the density distribution for the observed data.  A density distribution assigns densities to an observed distribution that does not fit a mathematical sampling distribution like the standard normal distribution.   We use the Kernel Density Estimation method implemented in the R base package.

The grey line shows the predicted density distribution based on Uli’s z-curve method.  The z-curve plot makes it easy to see the fit of the model to the data, which is typically very good.  The model result of the model is the weighted average of the true power that corresponds to the center of the simulated normal distributions.  For this distribution,  the weighted average is 48%.

The 48% estimate can be interpreted in two ways.  First, it means that if researchers randomly sampled from the set of studies in social psychology and were able to exactly reproduce the original study (including sample size),  they have a probability of 48% to replicate a significant result with alpha = .05.  The complementary interpretation is that if researchers were successful in replicating all studies exactly,  the reproducibility project is expected to produce 48% significant results and 52% non-significant results.  Because average power of studies predicts the success of exact replication studies, Jerry and I refer to the average power of studies that were selected for significance replicability.  Simulation studies show that our z-curve methods have good large sample accuracy (+/- 2%) and we adjust for the small estimation bias in large samples by computing a conservative confidence interval that adds 2% to the upper limit and 2% to the lower limit.

Below is the R-Code to obtain estimates of replicability from a set of z-values using Uli’s method.

<<<Download Zcurve R.Code>>>

Install R.Code on your computer, then run from anywhere with the following code

location =  <user folder>  #provide location information where z-curve code is stored
source(paste0(location,”fun.uli.zcurve.sharing.18.1.R”))  #read the code
run.zcurve(z.val.input)  #get z-curve estimates with z-values as input






















A critique of Stroebe and Strack’s Article “The Alleged Crisis and the Illusion of Exact Replication”

The article by Stroebe and Strack (2014) [henceforth S&S] illustrates how experimental social psychologists responded to replication failures in the beginning of the replicability revolution.  The response is a classic example of repressive coping: Houston, we do not have a problem. Even in 2014,  problems with the way experimental social psychologists had conducted research for decades were obvious (Bem, 2011; Wagenmakers et al., 2011; John et al., 2012; Francis, 2012; Schimmack, 2012; Hasher & Wagenmakers, 2012).  S&S article is an attempt to dismiss these concerns as misunderstandings and empirically unsupported criticism.

“In contrast to the prevalent sentiment, we will argue that the claim of a replicability crisis is greatly exaggerated” (p. 59).  

Although the article was well received by prominent experimental social psychologists (see citations in appendix), future events proved S&S wrong and vindicated critics of research methods in experimental social psychology. Only a year later, the Open Science Collaboration (2015) reported that only 25% of studies in social psychology could be replicated successfully.  A statistical analysis of focal hypothesis tests in social psychology suggests that roughly 50% of original studies could be replicated successfully if these studies were replicated exactly (Motyl et al., 2017).  Ironically, one of S&S’s point is that exact replication studies are impossible. As a result, the 50% estimate is an optimistic estimate of the success rate for actual replication studies, suggesting that the actual replicability of published results in social psychology is less than 50%.

Thus, even if S&S had reasons to be skeptical about the extent of the replicability crisis in experimental social psychology, it is now clear that experimental social psychology has a serious replication problem. Many published findings in social psychology textbooks may not replicate and many theoretical claims in social psychology rest on shaky empirical foundations.

What explains the replication problem in experimental social psychology?  The main reason for replication failures is that social psychology journals mostly published significant results.  The selective publishing of significant results is called publication bias. Sterling pointed out that publication bias in psychology is rampant.  He found that psychology journals publish over 90% significant results (Sterling, 1959; Sterling et al., 1995).  Given new estimates that the actual success rate of studies in experimental social psychology is less than 50%, only publication bias can explain why journals publish over 90% results that confirm theoretical predictions.

It is not difficult to see that reporting only studies that confirm predictions undermines the purpose of empirical tests of theoretical predictions.  If studies that do not confirm predictions are hidden, it is impossible to obtain empirical evidence that a theory is wrong.  In short, for decades experimental social psychologists have engaged in a charade that pretends that theories are empirically tested, but publication bias ensured that theories would never fail.  This is rather similar to Volkswagen’s emission tests that were rigged to pass because emissions were never subjected to a real test.

In 2014, there were ample warning signs that publication bias and other dubious practices inflated the success rate in social psychology journals.  However, S&S claim that (a) there is no evidence for the use of questionable research practices and (b) that it is unclear which practices are questionable or not.

“Thus far, however, no solid data exist on the prevalence of such research practices in either social or any other area of psychology. In fact, the discipline still needs to reach an agreement about the conditions under which these practices are unacceptable” (p. 60).

Scientists like to hedge their statements so that they are immune to criticism. S&S may argue that the evidence in 2014 was not “solid” and surely there was and still is no agreement about good research practices. However, this is irrelevant. What is important is that success rates in social psychology journals were and still are inflated by suppressing disconfirming evidence and biasing empirical tests of theories in favor of positive outcomes.

Although S&S’s main claims are not based on empirical evidence, it is instructive to examine how they tried to shield published results and established theories from the harsh light of open replication studies that report results without selection for significance and subject social psychological theories to real empirical tests for the first time.

Failed Replication of Between-Subject Priming Studies

S&S discuss failed replications of two famous priming studies in social psychology: Bargh’s elderly priming study and Dijksterhuis’s professor priming studies.  Both seminal articles reported several successful tests of the prediction that a subtle priming manipulation would influence behavior without participants even noticing the priming effect.  In 2012, Doyen et al., failed to replicate elderly priming. Schanks et al. (2013) failed to replicate professor priming effects and more recently a large registered replication report also provided no evidence for professor priming.  For naïve readers it is surprising that original studies had a 100% success rate and replication studies had a 0% success rate.  However, S&S are not surprised at all.

“as in most sciences, empirical findings cannot always be replicated” (p. 60). 

Apparently, S&S knows something that naïve readers do not know.  The difference between naïve readers and experts in the field is that experts have access to unpublished information about failed replications in their own labs and in the labs of their colleagues. Only they know how hard it sometimes was to get the successful outcomes that were published. With the added advantage of insider knowledge, it makes perfect sense to expect replication failures, although may be not 0%.

The problem is that S&S give the impression that replication failures are too be expected, but that this expectation cannot be based on the objective scientific record that hardly ever reports results that contradict theoretical predictions.  Replication failures occur all the time, but they remained unpublished. Doyen et al. and Schanks et al.’s articles only violated the code to publish only supportive evidence.

Kahneman’s Train Wreck Letter

S&S also comment on Kahneman’s letter to Bargh that compared priming research to a train wreck.  In response S&S claim that

“priming is an entirely undisputed method that is widely used to test hypotheses about associative memory (e.g., Higgins, Rholes, & Jones, 1977; Meyer & Schvaneveldt, 1971; Tulving & Schacter, 1990).” (p. 60).  

This argument does not stand the test of time.  Since S&S published their article researchers have distinguished more clearly between highly replicable priming effects in cognitive psychology with repeated measures and within-subject designs and difficult to replicate between-subject social priming studies with subtle priming manipulations and a single outcome measure (BS social priming).  With regards to BS social priming, it is unclear which of these effects can be replicated and leading social psychologists have been reluctant to demonstrate replicability of their famous studies by conducting self-replications as they were encouraged to do in Kahneman’s letter.

S&S also point to empirical evidence for robust priming effects.

“A meta-analysis of studies that investigated how trait primes influence impression formation identified 47 articles based on 6,833 participants and found overall effects to be statistically highly significant (DeCoster & Claypool, 2004).” (p. 60). 

The problem with this evidence is that this meta-analysis did not take publication bias into account; in fact, it does not even mention publication bias as a possible problem.  A meta-analysis of studies that were selected for significance produces is also biased by selection for significance.

Several years after Kahneman’s letter, it is widely agreed that past research on social priming is a train wreck.  Kahneman published a popular book that celebrated social priming effects as a major scientific discovery in psychology.  Nowadays, he agrees with critiques that the existing evidence is not credible.  It is also noteworthy that none of the researchers in this area have followed Kahneman’s advice to replicate their own findings to show the world that these effects are real.

It is all a big misunderstanding

S&S suggest that “the claim of a replicability crisis in psychology is based on a major misunderstanding.” (p. 60). 

Apparently, lay people, trained psychologists, and a Noble laureate are mistaken in their interpretation of replication failures.  S&S suggest that failed replications are unimportant.

“the myopic focus on “exact” replications neglects basic epistemological principles” (p. 60).  

To make their argument, they introduce the notion of exact replications and suggest that exact replication studies are uninformative.

 “a finding may be eminently reproducible and yet constitute a poor test of a theory.” (p. 60).

The problem with this line of argument is that we are supposed to assume that a finding is eminently reproducible, which probably means it has been successfully replicate many times.  It seems sensible that further studies of gender differences in height are unnecessary to convince us that there is a gender difference in height. However, results in social psychology are not like gender differences in height.  According to S&S own accord earlier, “empirical findings cannot always be replicated” (p. 60). And if journals only publish significant results, it remains unknown which results are eminently reproducible and which results are not.  S&S ignore publication bias and pretend that the published record suggests that all findings in social psychology are eminently reproducible. Apparently, they would suggest that even Bem’s findings that people have supernatural abilities is eminently reproducible.  These days, few social psychologists are willing to endorse this naïve interpretation of the scientific record as a credible body of empirical facts.   

Exact Replication Studies are Meaningful if they are Successful

Ironically, S&S next suggest that exact replication studies can be useful.

Exact replications are also important when studies produce findings that are unexpected and only loosely connected to a theoretical framework. Thus, the fact that priming individuals with the stereotype of the elderly resulted in a reduction of walking speed was a finding that was unexpected. Furthermore, even though it was consistent with existing theoretical knowledge, there was no consensus about the processes that mediate the impact of the prime on walking speed. It was therefore important that Bargh et al. (1996) published an exact replication of their experiment in the same paper.

Similarly, Dijksterhuis and van Knippenberg (1998) conducted four studies in which they replicated the priming effects. Three of these studies contained conditions that were exact replications.

Because it is standard practice in publications of new effects, especially of effects that are surprising, to publish one or two exact replications, it is clearly more conducive to the advancement of psychological knowledge to conduct conceptual replications rather than attempting further duplications of the original study.

Given these citations it is problematic that S&S article is often cited to claim that exact replications are impossible or unnecessary.  The argument that S&S are making here is rather different.  They are suggesting that original articles already provide sufficient evidence that results in social psychology are eminently reproducible because original articles report multiple studies and some of these studies are often exact replication studies.  At face value, S&S have a point.  An honest series of statistically significant results makes it practically impossible that an effect is a false positive result (Schimmack, 2012).  The problem is that multiple study articles are not honest reports of all replication attempts.  Francis (2014) found that at least 80% of multiple study articles showed statistical evidence of questionable research practices.  Given the pervasive influence of selection for significance, exact replication studies in original articles provide no information about the replicability of these results.

What made the failed replications by Doyen et al. and Shank et al. so powerful was that these studies were the first real empirical tests of BS social priming effects because the authors were willing to report successes or failures.  The problem for social psychology is that many textbook findings that were obtained with selection for significance cannot be reproduced in honest empirical tests of the predicted effects.  This means that the original effects were either dramatically inflated or may not exist at all.

Replication Studies are a Waste of Resources

S&S want readers to believe that replication studies are a waste of resources.

Given that both research time and money are scarce resources, the large scale attempts at duplicating previous studies seem to us misguided” (p. 61).

This statement sounds a bit like a plea to spare social psychology from the embarrassment of actual empirical tests that reveal the true replicability of textbook findings. After all, according to S&S it is impossible to duplicate original studies (i.e., conduct exact replication studies) because replication studies differ in some way from original studies and may not reproduce the original results.  So, none of the failed replication studies is an exact replication.  Doyen et al. replicate Bargh’s study that was conducted in New York city in Belgium and Shanks et al. replicated Dijksterhuis’s studies from the Netherlands in the United States.  The finding that the original results could not be replicate the original results does not imply that the original findings were false positives, but they do imply that these findings may be unique to some unspecified specifics of the original studies.  This is noteworthy when original results are used in textbook as evidence for general theories and not as historical accounts of what happened in one specific socio-cultural context during a specific historic period. As social situations and human behavior are never exact replications of the past, social psychological results need to be permanently replicated and doing so is not a waste of resources.  Suggesting that replications is a waste of resources is like suggesting that measuring GDP or unemployment every year is a waste of resources because we can just use last-year’s numbers.

As S&S ignore publication bias and selection for significance, they are also ignoring that publication bias leads to a massive waste of resources.  First, running empirical tests of theories that are not reported is a waste of resources.  Second, publishing only significant results is also a waste of resources because researchers design new studies based on the published record. When the published record is biased, many new studies will fail, just like airplanes who are designed based on flawed science would drop from the sky.  Thus, a biased literature creates a massive waste of resources.

Ultimately, a science that publishes only significant result wastes all resources because the outcome of the published studies is a foregone conclusion: the prediction was supported, p < .05. Social psychologists might as well publish purely theoretical article, just like philosophers in the old days used “thought experiments” to support their claims. An empirical science is only a real science if theoretical predictions are subjected to tests that can fail.  By this simple criterion, experimental social psychology is not (yet) a science.

Should Psychologists Conduct Exact Replications or Conceptual Replications?

Strobe and Strack’s next cite Pashler and Harris (2012) to claim that critiques of experimental social psychology have dismissed the value of so-called conceptual replications and generalize.

The main criticism of conceptual replications is that they are less informative than exact replications (e.g., Pashler & Harris, 2012).” 

Before I examine S&S’s counterargument, it is important to realize that S&S misrepresented, and maybe misunderstood, Pashler and Harris’s main point. Here is the relevant quote from Pashler and Harris’s article.

We speculate that the harmful interaction of publication bias and a focus on conceptual rather than direct replications may even shed light on some of the famous and puzzling “pathological science” cases that embarrassed the natural sciences at several points in the 20th century (e.g., Polywater; Rousseau & Porto, 1970; and cold fusion; Taubes, 1993).

The problem for S&S is that they cannot address the problem of publication bias and therefore carefully avoid talking about it.  As a result, they misrepresent Pashler and Harris’s critique of conceptual replications in combination with publication bias as a criticism of conceptual replication studies, which is absurd and not what Pashler and Harris’s intended to say or actually said. The following quote from their article makes this crystal clear.

However, what kept faith in cold fusion alive for some time (at least in the eyes of some onlookers) was a trickle of positive results achieved using very different designs than the originals (i.e., what psychologists would call conceptual replications). This suggests that one important hint that a controversial finding is pathological may arise when defenders of a controversial effect disavow the initial methods used to obtain an effect and rest their case entirely upon later studies conducted using other methods. Of course, productive research into real phenomena often yields more refined and better ways of producing effects. But what should inspire doubt is any situation where defenders present a phenomenon as a “moving target” in terms of where and how it is elicited (cf. Langmuir, 1953/1989). When this happens, it would seem sensible to ask, “If the finding is real and yet the methods used by the original investigators are not reproducible, then how were these investigators able to uncover a valid phenomenon with methods that do not work?” Again, the unavoidable conclusion is that a sound assessment of a controversial phenomenon should focus first and foremost on direct replications of the original reports and not on novel variations, each of which may introduce independent ambiguities.

I am confident that unbiased readers will recognize that Pashler and Harris did not suggest that conceptual replication studies are bad.  Their main point is that a few successful conceptual replication studies can be used to keep theories alive in the face of a string of many replication failures. The problem is not that researchers conduct successful conceptual replication studies. The problem is dismissing or outright hiding of disconfirming evidence in replication studies. S&S misconstrue Pashler and Harris’s claim to avoid addressing this real problem of ignoring and suppressing failed studies to support an attractive but false theory.

The illusion of exact replications.

S&S next argument is that replication studies are never exact.

If one accepts that the true purpose of replications is a (repeated) test of a theoretical hypothesis rather than an assessment of the reliability of a particular experimental procedure, a major problem of exact replications becomes apparent: Repeating a specific operationalization of a theoretical construct at a different point in time and/or with a different population of participants might not reflect the same theoretical construct that the same procedure operationalized in the original study.

The most important word in this quote is “might.”   Ebbinghaus’s memory curve MIGHT not replicate today because he was his own subject.  Bargh’s elderly priming study MIGHT not work today because Florida is no longer associated with the elderly, and Disjterhuis’s priming study MIGHT no longer works because students no longer think that professors are smart or that Hooligans are dumb.

Just because there is no certainty in inductive inferences doesn’t mean we can just dismiss replication failures because something MIGHT have changed.  It is also possible that the published results MIGHT be false positives because significant results were obtained by chance, with QRPs, or outright fraud.  Most people think that outright fraud is unlikely, but the Stapel debacle showed that we cannot rule it out.  So, we can argue forever about hypothetical reasons why a particular study was successful or a failure. These arguments are futile and have nothing to do with scientific arguments and objective evaluation of facts.

This means that every study, whether it is a groundbreaking success or a replication failure needs to be evaluate in terms of the objective scientific facts. There is no blanket immunity for seminal studies that protects them from disconfirming evidence.  No study is an exact replication of another study. That is a truism and S&S article is often cited for this simple fact.  It is as true as it is irrelevant to understand the replication crisis in social psychology.

Exact Replications Are Often Uninformative

S&S contradict themselves in the use of the term exact replication.  First it is impossible to do exact replications, but then they are uninformative.  I agree with S&S that exact replication studies are impossible. So, we can simply drop the term “exact” and examine why S&S believe that some replication studies are uninformative.

First they give an elaborate, long and hypothetical explanation for Doyen et al.’s failure to replicate Bargh’s pair of elderly priming studies. After considering some possible explanations, they conclude

It is therefore possible that the priming procedure used in the Doyen et al. (2012) study failed in this respect, even though Doyen et al. faithfully replicated the priming procedure of Bargh et al. (1996).  

Once more the realm of hypothetical conjectures has to rescue seminal findings. Just as it is possible that S&S are right it is also possible that Bargh faked his data. To be sure, I do not believe that he faked his data and I apologized for a Facebook comment that gave the wrong impression that I did. I am only raising this possibility here to make the point that everything is possible. Maybe Bargh just got lucky.  The probability of this is 1 out of 1,600 attempts (the probability to get the predicted effect with .05 two-tailed (!) twice is .025^2). Not very likely, but also not impossible.

No matter what the reason for the discrepancy between Bargh and Doyen’s findings is, the example does not support S&S’s claim that replication studies are uninformative. The failed replication raised concerns about the robustness of BS social priming studies and stimulated further investigation of the robustness of social priming effects. In the short span of six years, the scientific consensus about these effects has shifted dramatically, and the first publication of a failed replication is an important event in the history of social psychology.

S&S’s critique of Shank et al.’s replication studies is even weaker.  First, they have to admit that professor probably still primes intelligence more than soccer hooligans. To rescue the original finding S&S propose

“the priming manipulation might have failed to increase the cognitive representation of the concept “intelligence.” 

S&S also think that

another LIKELY reason for their failure could be their selection of knowledge items.

Meanwhile a registered replication report with a design that was approved by Dijksterhuis failed to replicate the effect.  Although it is possible to come up with more possible reasons for these failures, real scientific creativity is revealed in creating experimental paradigms that produce replicable results, not in coming up with many post-hoc explanations for replication failures.

Ironically, S&S even agree with my criticism of their argument.

 “To be sure, these possibilities are speculative”  (p. 62). 

In contrast, S&S fail to consider the possibility that published significant results are false positives, even though there is actual evidence for publication bias. The strong bias against published failures may be rooted in a long history of dismissing unpublished failures that social psychologists routinely encounter in their own laboratory.  To avoid the self-awareness that hiding disconfirming evidence is unscientific, social psychologists made themselves believe that minute changes in experimental procedures can ruin a study (Stapel).  Unfortunately, a science that dismisses replication failures as procedural hiccups is fated to fail because it removed the mechanism that makes science self-correcting.

Failed Replications are Uninformative

S&S next suggest that “nonreplications are uninformative unless one can demonstrate that the theoretically relevant conditions were met” (p. 62).

This reverses the burden of proof.  Original researchers pride themselves on innovative ideas and groundbreaking discoveries.  Like famous rock stars, they are often not the best musicians, nor is it impossible for other musicians to play their songs. They get rewarded because they came up with something original. Take the Implicit Association Test as an example. The idea to use cognitive switching tasks to measure attitudes was original and Greenwald deserves recognition for inventing this task. The IAT did not revolutionize attitude research because only Tony Greenwald could get the effects. It did so because everybody, including my undergraduate students, could replicate the basic IAT effect.

However, let’s assume that the IAT effect could not have been replicated. Is it really the job of researchers who merely duplicated a study to figure out why it did not work and develop a theory under which circumstances an effect may occur or not?  I do not think so. Failed replications are informative even if there is no immediate explanation why the replication failed.  As Pashler and Harris’s cold fusion example shows there may not even be a satisfactory explanation after decades of research. Most probably, cold fusion never really worked and the successful outcome of the original study was a fluke or a problem of the experimental design.  Nevertheless, it was important to demonstrate that the original cold fusion study could not be replicated.  To ask for an explanation why replication studies fail is simply a way to make replication studies unattractive and to dismiss the results of studies that fail to produce the desired outcome.

Finally, S&S ignore that there is a simple explanation for replication failures in experimental social psychology: publication bias.  If original studies have low statistical power (e.g., Bargh’s studies with N = 30) to detect small effects, only vastly inflated effect sizes reach significance.  An open replication study without inflated effect sizes is unlikely to produce a successful outcome. Statistical analysis of original studies show that this explanation accounts for a large proportion of replication failures. Thus, publication bias provides one explanation for replication failures.

Conceptual Replication Studies are Informative

S&S cite Schmidt (2009) to argue that conceptual replication studies are informative.

With every difference that is introduced the confirmatory power of the replication increases, because we have shown that the phenomenon does not hinge on a particular operationalization but “generalizes to a larger area of application” (p. 93).

S&S continue

“An even more effective strategy to increase our trust in a theory is to test it using completely different manipulations.”

This is of course true as long as conceptual replication studies are successful. However, it is not clear why conceptual replication studies that for the first time try a completely different manipulation should be successful.  As I pointed out in my 2012 article, reading multiple-study articles with only successful conceptual replication studies is a bit like watching a magic show.

Multiple-study articles are most common in experimental psychology to demonstrate the robustness of a phenomenon using slightly different experimental manipulations. For example, Bem (2011) used a variety of paradigms to examine ESP. Demonstrating a phenomenon in several different ways can show that a finding is not limited to very specific experimental conditions. Analogously, if Joe can hit the bull’s-eye nine times from different angles, with different guns, and in different light conditions, Joe truly must be a sharpshooter. However, the variation of experimental procedures also introduces more opportunities for biases (Ioannidis, 2005). The reason is that variation of experimental procedures allows researchers to discount null findings. Namely, it is possible to attribute nonsignificant results to problems with the experimental procedure rather than to the absence of an effect.

I don’t know whether S&S are impressed by Bem’s article with 9 conceptual replication studies that successfully demonstrated supernatural abilities.  According to their line of arguments, they should be.  However, even most social psychologists found it impossible to accept that time-reversed subliminal priming works. Unfortunately, this also means that successful conceptual replication studies are meaningless if only successful results are published.  Once more, S&S cannot address this problem because they ignore the simple fact that selection for significance undermines the purpose of empirical research to test theoretical predictions.

Exact Replications Contribute Little to Scientific Knowledge

Without providing much evidence for their claims, S&S conclude

one reason why exact replications are not very interesting is that they contribute little to scientific knowledge.

Ironically, one year later Science published 100 replication studies with the only goal of estimating the replicability of psychology, with a focus on social psychology.  The article has already been cited 640 times, while S&S’s criticism of replication studies has been cited (only) 114 times.

Although the article did nothing else then to report the outcome of replication studies, it made a tremendous empirical contribution to psychology because it reported results of studies without the filter of publication bias.  Suddenly the success rate plummeted from over 90% to 37% and for social psychology to 25%.  While S&S could claim in 2014 that “Thus far, however, no solid data exist on the prevalence of such [questionable] research practices in either social or any other area of psychology,” the reproducibility project revealed that these practices dramatically inflated the percentage of successful studies reported in psychology journals.

The article has been celebrated by scientists in many disciplines as a heroic effort and a sign that psychologists are trying to improve their research practices. S&S may disagree, but I consider the reproducibility project a big contribution to scientific knowledge.

Why null findings are not always that informative

To fully appreciate the absurdity of S&S’s argument, I let them speak for themselves.

One reason is that not all null findings are interesting.  For example, just before his downfall, Stapel published an article on how disordered contexts promote stereotyping and discrimination. In this publication, Stapel and Lindenberg (2011) reported findings showing that litter or a broken-up sidewalk and an abandoned bicycle can increase social discrimination. These findings, which were later retracted, were judged to be sufficiently important and interesting to be published in the highly prestigious journal Science. Let us assume that Stapel had actually conducted the research described in this paper and failed to support his hypothesis. Such a null finding would have hardly merited publication in the Journal of Articles in Support of the Null Hypothesis. It would have been uninteresting for the same reason that made the positive result interesting, namely, that (a) nobody expected a relationship between disordered environments and prejudice and (b) there was no previous empirical evidence for such a relationship. Similarly, if Bargh et al. (1996) had found that priming participants with the stereotype of the elderly did not influence walking speed or if Dijksterhuis and van Knippenberg (1998) had reported that priming participants with “professor” did not improve their performance on a task of trivial pursuit, nobody would have been interested in their findings.

Notably, all of the examples are null-findings in original studies. Thus, they have absolutely no relevance for the importance of replication studies. As noted by Strack and Stroebe earlier

Thus, null findings are interesting only if they contradict a central hypothesis derived from an established theory and/or are discrepant with a series of earlier studies.” (p. 65). 

Bem (2011) reported 9 significant results to support unbelievable claims about supernatural abilities.  However, several failed replication studies allowed psychologists to dismiss these findings and to ignore claims about time-reversed priming effects. So, while not all null-results are important, null-results in replication studies are important because they can correct false positive results in original articles. Without this correction mechanism, science looses its ability to correct itself.

Failed Replications Do Not Falsify Theories

S&S state that failed replications do not falsify theories

The nonreplications published by Shanks and colleagues (2013) cannot be taken as a falsification of that theory, because their study does not explain why previous research was successful in replicating the original findings of Dijksterhuis and van Knippenberg (1998).” (p. 64). 

I am unaware of any theory in psychology that has been falsified. The reason for this is not that failed replication studies are not informative. The reason is that theories have been protected by hiding failed replication studies until recently. Only in recent years have social psychologists started to contemplate the possibility that some theories in social psychology might be false.  The most prominent example is ego-depletion theory, which has been one of the first prominent theories that has been put under the microscope of open science without the protection of questionable research practices in recent years. While ego-depletion theory is not entirely dead, few people still believe in the simple theory that 20 Stroop trials deplete individuals’ will power.  Falsification is hard, but falsification without disconfirming evidence is impossible.

Inconsistent Evidence

S&S argue that replication failures have to be evaluated in the context of replication successes.

Even multiple failures to replicate an established finding would not result in a rejection of the original hypothesis, if there are also multiple studies that supported that hypothesis. 

Earlier S&S wrote

in social psychology, as in most sciences, empirical findings cannot always be replicated (this was one of the reasons for the development of meta-analytic methods). 

Indeed. Unless studies have very high statistical power, inconsistent results are inevitable; which is one reason why publishing only significant results is a sign of low credibility (Schimmack, 2012). Meta-analysis is the only way to make sense of these inconsistent findings.  However, it is well known that publication bias makes meta-analytic results meaningless (e.g., meta-analysis show very strong evidence for supernatural abilities).  Thus, it is important that all tests of a theoretical prediction are reported to produce meaningful meta-analyses.  If social psychologists would take S&S seriously and continue to suppress non-significant results because they are uninformative, meta-analysis would continue to provide biased results that support even false theories.

Failed Replications are Uninformative II

Sorry that this is getting really long. But S&S keep on making the same arguments and the editor of this article didn’t tell them to shorten the article. Here they repeat the argument that failed replications are uninformative.

One reason why null findings are not very interesting is because they tell us only that a finding could not be replicated but not why this was the case. This conflict can be resolved only if researchers develop a theory that could explain the inconsistency in findings.  

A related claim is that failed replications never demonstrate that original findings were false because the inconsistency is always due to some third variable; a hidden moderator.

Methodologically, however, nonreplications must be understood as interaction effects in that they suggest that the effect of the crucial influence depends on the idiosyncratic conditions under which the original experiment was conducted” (p. 64). 

These statements reveal a fundamental misunderstanding of statistical inferences.  A significant result never proofs that the null-hypothesis is false.  The inference that a real effect rather than sampling error caused the observed result can be a mistake. This mistake is called a false positive or a type-I error. S&S seems to believe that type-I errors do not exist. Accordingly, Bem’s significant results show real supernatural abilities.  If this were the case, it would be meaningless to report statistical significance tests. The only possible error that could be made would be false negatives or type-II error; the theory makes the correct prediction, but a study failed to produce a significant result. And if theoretical predictions are always correct, it is also not necessary to subject theories to empirical tests, because these tests either correctly show that a prediction was confirmed or falsely fail to confirm a prediction.

S&S’s belief in published results has a religious quality.  Apparently we know nothing about the world, but once a significant result is published in a social psychology journal, ideally JPSP, it becomes a holy truth that defies any evidence that non-believers may produce under the misguided assumption that further inquiry is necessary. Elderly priming is real, amen.

More Confusing Nonsense

At some point, I was no longer surprised by S&S’s claims, but I did start to wonder about the reviewers and editors who allowed this manuscript to be published apparently with light or no editing.  Why would a self-respecting journal publish a sentence like this?

As a consequence, the mere coexistence of exact replications that are both successful and unsuccessful is likely to leave researchers helpless about what to conclude from such a pattern of outcomes.

Didn’t S&S claim that exact replication studies do not exist? Didn’t they tell readers that every inconsistent finding has to be interpreted as an interaction effect?  And where do they see inconsistent results if journals never publish non-significant results?

Aside from these inconsistencies, inconsistent results do not lead to a state of helpless paralysis. As S&S suggested themselves, they conduct a meta-analysis. Are S&S suggesting that we need to spare researchers from inconsistent results to protect them from a state of helpless confusion? Is this their justification for publishing only significant results?

Even Massive Replication Failures in Registered Replication Reports are Uninformative

In response to the replication crisis, some psychologists started to invest time and resources in major replication studies called many lab studies or registered replication studies.  A single study was replicated in many labs.  The total sample size of many labs gives these studies high precision in estimating the average effect size and makes it even possible to demonstrate that an effect size is close to zero, which suggests that the null-hypothesis may be true.  These studies have failed to find evidence for classic social psychology findings, including Strack’s facial feedback studies. S&S suggest that even these results are uninformative.

Conducting exact replications in a registered and coordinated fashion by different laboratories does not remove the described shortcomings. This is also the case if exact replications are proposed as a means to estimate the “true size” of an effect. As the size of an experimental effect always depends on the specific error variance that is generated by the context, exact replications can assess only the efficiency of an intervention in a given situation but not the generalized strength of a causal influence.

Their argument does not make any sense to me.  First, it is not clear what S&S mean by “the size of an experimental effect always depends on the specific error variance.”  Neither unstandardized nor standardized effect sizes depend on the error variance. This is simple to see because error variance depends on the sample size and effect sizes do not depend on sample size.  So, it makes no sense to claim that effect sizes depend on error variance.

Second, it is not clear what S&S mean by specific error variance that is generated by the context.  I simply cannot address this argument because the notion of context generated specific error variance is not a statistical construct and S&S do not explain what they are talking about.

Finally, it is not clear why meta-analysis of replication studies cannot be used to estimate the generalized strength of a causal influence, which I believe to mean “an effect size”?  Earlier S&S alluded to meta-analysis as a way to resolve inconsistencies in the literature, but now they seem to suggest that meta-analysis cannot be used.

If S&S really want to imply that meta-analyses are useless, it is unclear how they would make sense of inconsistent findings.  The only viable solution seems to be to avoid inconsistencies by suppressing non-significant results in order to give the impression that every theory in social psychology is correct because theoretical predictions are always confirmed.  Although this sounds absurd, it is the inevitable logical consequence of S&S’s claim that non-significant results are uninformative, even if over 20 labs independently and in combination failed to provide evidence for a theoretical predicted effect.

The Great History of Social Psychological Theories

S&S next present Über-social psychologist, Leon Festinger, as an example why theories are good and failed studies are bad.  The argument is that good theories make correct predictions, even if bad studies fail to show the effect.

“Although their theoretical analysis was valid, it took a decade before researchers were able to reliably replicate the findings reported by Festinger and Carlsmith (1959).”

As a former student, I was surprised by this statement because I had learned that Festinger’s theory was challenged by Bem’s theory and that social psychologists had been unable to resolve which of the two theories was correct.  Couldn’t some of these replication failures be explained by the fact that Festinger’s theory sometimes made the wrong prediction?

It is also not surprising that researchers had a hard time replicating Festinger and Carlsmith original findings.  The reason is that the original study had low statistical power and replication failures are expected even if the theory is correct. Finally, I have been around social psychologists long enough to have heard some rumors about Festinger and Carlsmith’s original studies.  Accordingly, some of Festinger’s graduate students also tried and failed to get the effect. Carlsmith was the ‘lucky’ one who got the effect, in one study p < .05, and he became the co-author of one of the most cited articles in the history of social psychology. Naturally, Festinger did not publish the failed studies of his other graduate students because surely they must have done something wrong. As I said, that is a rumor.  Even if the rumor is not true, and Carlsmith got lucky on the first try, luck played a factor and nobody should expect that a study replicates simply because a single published study reported a p-value less than .05.

Failed Replications Did Not Influence Social Psychological Theories

Argument quality reaches a new low with the next argument against replication studies.

 “If we look at the history of social psychology, theories have rarely been abandoned because of failed replications.”

This is true, but it reveals the lack of progress in theory development in social psychology rather than the futility of replication studies.  From an evolutionary perspective, theory development requires selection pressure, but publication bias protects bad theories from failure.

The short history of open science shows how weak social psychological theories are and that even the most basic predictions cannot be confirmed in open replication studies that do not selectively report significant results.  So, even if it is true that failed replications have played a minor role in the past of social psychology, they are going to play a much bigger role in the future of social psychology.

The Red Herring: Fraud

S&S imply that Roediger suggested to use replication studies as a fraud detection tool.

if others had tried to replicate his [Stapel’s] work soon after its publication, his misdeeds might have been uncovered much more quickly

S&S dismiss this idea in part on the basis of Stroebe’s research on fraud detection.

To their own surprise, Stroebe and colleagues found that replications hardly played any role in the discovery of these fraud cases.

Now this is actually not surprising because failed replications were hardly ever published.  And if there is no variance in a predictor variable (significance), we cannot see a correlation between the predictor variable and an outcome (fraud).  Although failed replication studies may help to detect fraud in the future, this is neither their primary purpose, nor necessary to make replication studies valuable. Replication studies also do not bring world peace or bring an end to global warming.

For some inexplicable reason S&S continue to focus on fraud. For example, they also argue that meta-analyses are poor fraud detectors, which is as true as it is irrelevant.

They conclude their discussion with an observation by Stapel, who famously faked 50+ articles in social psychology journals.

As Stapel wrote in his autobiography, he was always pleased when his invented findings were replicated: “What seemed logical and was fantasized became true” (Stapel, 2012). Thus, neither can failures to replicate a research finding be used as indicators of fraud, nor can successful replications be invoked as indication that the original study was honestly conducted.

I am not sure why S&S spend so much time talking about fraud, but it is the only questionable research practice that they openly address.  In contrast, they do not discuss other questionable research practices, including suppressing failed studies, that are much more prevalent and much more important for the understanding of the replication crisis in social psychology than fraud.  The term “publication bias” is not mentioned once in the article. Sometimes what is hidden is more significant than what is being published.


The conclusion section correctly predicts that the results of the reproducibility project will make social psychology look bad and that social psychology will look worse than other areas of psychology.

But whereas it will certainly be useful to be informed about studies that are difficult to replicate, we are less confident about whether the investment of time and effort of the volunteers of the Open Science Collaboration is well spent on replicating studies published in three psychology journals. The result will be a reproducibility coefficient that will not be greatly informative, because of justified doubts about whether the “exact” replications succeeded in replicating the theoretical conditions realized in the original research.

As social psychologists, we are particularly concerned that one of the outcomes of this effort will be that results from our field will be perceived to be less “reproducible” than research in other areas of psychology. This is to be expected because for the reasons discussed earlier, attempts at “direct” replications of social psychological studies are less likely than exact replications of experiments in psychophysics to replicate the theoretical conditions that were established in the original study.

Although psychologists should not be complacent, there seem to be no reasons to panic the field into another crisis. Crises in psychology are not caused by methodological flaws but by the way people talk about them (Kruglanski & Stroebe, 2012).

S&S attribute the foreseen (how did they know?) bad outcome in the reproducibility project to the difficulty of replicating social psychological studies, but they fail to explain why social psychology journals publish as many successes as other disciplines.

The results of the reproducibility project provide an answer to this question.  Social psychologists use designs with less statistical power that have a lower chance of producing a significant result. Selection for significance ensures that the success rate is equally high in all areas of psychology, but lower power makes these successes less replicable.

To avoid further embarrassments in an increasingly open science, social psychologists must improve the statistical power of their studies. Which social psychological theories will survive actual empirical tests in the new world of open science is unclear.  In this regard, I think it makes more sense to compare social psychology to a ship wreck than a train wreck.  Somewhere down on the floor of the ocean is some gold. But it will take some deep diving and many failed attempts to find it.  Good luck!


S&S’s article was published in a “prestigious” psychology journal and has already garnered 114 citations. It ranks #21 in my importance rankings of articles in meta-psychology.  So, I was curious why the article gets cited.  The appendix lists 51 citing articles with the relevant citation and the reason for citing S&S’s article.   The table shows the reasons for citations in decreasing order of frequency.

S&S are most frequently cited for the claim that exact replications are impossible, followed by the reason for this claim that effects in psychological research are sensitive to the unique context in which a study is conducted.  The next two reasons for citing the article are that only conceptual replications (CR) test theories, whereas the results of exact replications (ER) are uninformative.  The problem is that every study is a conceptual replication because exact replications are impossible. So, even if exact replications were uninformative this claim has no practical relevance because there are no exact replications.  Some articles cite S&S with no specific claim attached to the citation.  Only two articles cite them for the claim that there is no replication crisis and only 1 citation cites S&S for the claim that there is no evidence about the prevalence of QRPs.   In short, the article is mostly cited for the uncontroversial and inconsequential claim that exact replications are impossible and that effect sizes in psychological studies can vary as a function of unique features of a particular sample or study.  This observation is inconsequential because it is unclear how unknown unique characteristics of studies influence results.  The main implication of this observation is that study results will be more variable than we would expect from a set of exact replication studies. For this reason, meta-analysts often use random-effects model because fixed-effects meta-analysis assumes that all studies are exact replications.

ER impossible 11
Contextual Sensitivity 8
CR test theory 8
ER uninformative 7
Mention 6
ER/CR Distinction 2
No replication crisis 2
Disagreement 1
CR Definition 1
ER informative 1
ER useful for applied research 1
ER cannot detect fraud 1
No evidence about prevalence of QRP 1
Contextual sensitivity greater in social psychology 1

the most influential citing articles and the relevant citation.  I haven’t had time to do a content analysis, but the article is mostly cited to say (a) exact replications are impossible, and (b) conceptual replications are valuable, and (c) social psychological findings are harder to replicate.  Few articles cite to article to claim that the replication crisis is overblown or that failed replications are uninformative.  Thus, even though the article is cited a lot, it is not cited for the main points S&S tried to make.  The high number of citation therefore does not mean that S&S’s claims have been widely accepted.

The value of replication studies.

Simmons, DJ.
“In this commentary, I challenge these claims.”

(ER/CR Distinction)
Bilingualism and cognition.

Valian, V.
“A host of methodological issues should be resolved. One is whether the field should undertake exact replications, conceptual replications, or both, in order to determine the conditions under which effects are reliably obtained (Paap, 2014; Simons, 2014; Stroebe & Strack, 2014).”

(Contextual Sensitivity)
Is Psychology Suffering From a Replication Crisis? What Does “Failure to Replicate” Really Mean?“
Maxwell et al. (2015)
A particular replication may fail to confirm the results of an original study for a variety of reasons, some of which may include intentional differences in procedures, measures, or samples as in a conceptual replication (Cesario, 2014; Simons, 2014; Stroebe & Strack, 2014).”

(ER impossible)
The Chicago face database: A free stimulus set of faces and norming data 

Debbie S. Ma, Joshua Correll, & Bernd Wittenbrink.
The CFD will also make it easier to conduct exact replications, because researchers can use the same stimuli employed by other researchers (but see Stroebe & Strack, 2014).”

(Contextual Sensitivity)
“Contextual sensitivity in scientific reproducibility”
vanBavel et al. (2015)
“Many scientists have also argued that the failure to reproduce results might reflect contextual differences—often termed “hidden moderators”—between the original research and the replication attempt”

(Contextual Sensitivity)
Editorial Psychological Science

As Nosek and his coauthors made clear, even ideal replications of ideal studies are expected to fail some of the time (Francis, 2012), and failure to replicate a previously observed effect can arise from differences between the original and replication studies and hence do not necessarily indicate flaws in the original study (Maxwell, Lau, & Howard, 2015; Stroebe & Strack, 2014). Still, it seems likely that psychology journals have too often reported spurious effects arising from Type I errors (e.g., Francis, 2014).

(ER impossible)
Best Research Practices in Psychology: Illustrating Epistemological and Pragmatic Considerations With the Case of Relationship Science

Finkel et al. (2015).
“Nevertheless, many scholars believe that direct replications are impossible in the human sciences—S&S (2014) call them “an illusion”— because certain factors, such as a moment in historical time or the precise conditions under which a sample was obtained and tested, that may have contributed to a result can never be reproduced identically.”

Conceptualizing and evaluating the replication of research results
Fabrigar and Wegener (2016)
(CR test theory)
“Traditionally, the primary presumed strength of conceptual replications has been their ability to address issues of construct validity (e.g., Brewer & Crano, 2014; Schmidt, 2009; Stroebe & Strack, 2014). “

(ER impossible)
“First, it should be recognized that an exact replication in the strictest sense of the term can never be achieved as it will always be impossible to fully recreate the contextual factors and participant characteristics present in the original experiment (see Schmidt (2009); S&S (2014).”

(Contextual Sensitivity)
“S&S (2014) have argued that there is good reason to expect that many traditional and contemporary experimental manipulations in social psychology would have different psychological properties and effects if used in contexts or populations different from the original experiments for which they were developed. For example, classic dissonance manipulations and fear manipulations or more contemporary priming procedures might work very differently if used in new contexts and/or populations. One could generate many additional examples beyond those mentioned by S&S.”

(ER impossible)
“Another important point illustrated by the above example is that the distinction between exact and conceptual replications is much more nebulous than many discussions of replication would suggest. Indeed, some critics of the exact/conceptual replication distinction have gone so far as to argue that the concept of exact replication is an “illusion” (Stroebe & Strack, 2014). Though we see some utility in the exact/conceptual distinction (especially regarding the goal of the researcher in the work), we agree with the sentiments expressed by S&S. Classifying studies on the basis of the exact/conceptual distinction is more difficult than is often appreciated, and the presumed strengths and weaknesses of the approaches are less straightforward than is often asserted or assumed.”

(Contextual Sensitivity)
“Furthermore, assuming that these failed replication experiments have used the same operationalizations of the independent and dependent variables, the most common inference drawn from such failures is that confidence in the existence of the originally demonstrated effect should be substantially undermined (e.g., see Francis (2012); Schimmack (2012)). Alternatively, a more optimistic interpretation of such failed replication experiments could be that the failed versus successful experiments differ as a function of one or more unknown moderators that regulate the emergence of the effect (e.g., Cesario, 2014; Stroebe & Strack, 2014).”

Replicating Studies in Which Samples of Participants Respond to Samples of Stimuli.
(CR Definition)
Westfall et al. (2015).
Nevertheless, the original finding is considered to be conceptually replicated if it can be convincingly argued that the same theoretical constructs thought to account for the results of the original study also account for the results of the replication study (Stroebe & Strack, 2014). Conceptual replications are thus “replications” in the sense that they establish the reproducibility of theoretical interpretations.”

“Although establishing the generalizability of research findings is undoubtedly important work, it is not the focus of this article (for opposing viewpoints on the value of conceptual replications, see Pashler & Harris, 2012; Stroebe & Strack, 2014).“

Introduction to the Special Section on Advancing Our Methods and Practices
Ledgerwood, A.
We can and surely should debate which problems are most pressing and which solutions most suitable (e.g., Cesario, 2014; Fiedler, Kutzner, & Krueger, 2012; Murayama, Pekrun, & Fiedler, 2013; Stroebe & Strack, 2014). But at this point, most can agree that there are some real problems with the status quo.

***Theory Building, Replication, and Behavioral Priming: Where Do We Need to Go From Here?
Locke, EA
(ER impossible)
As can be inferred from Table 1, I believe that the now popular push toward “exact” replication (e.g., see Simons, 2014) is not the best way to go. Everyone agrees that literal replication is impossible (e.g., Stroebe & Strack, 2014), but let us assume it is as close as one can get. What has been achieved?

The War on Prevention: Bellicose Cancer: Metaphors Hurt (Some) Prevention Intentions”
(CR test theory)
David J. Hauser1 and Norbert Schwarz
“As noted in recent discussions (Stroebe & Strack, 2014), consistent effects of multiple operationalizations of a conceptual variable across diverse content domains are a crucial criterion for the robustness of a theoretical approach.”

Doyen et al. “
(CR test theory)
In contrast, social psychologists assume that the primes activate culturally and situationally contextualized representations (e.g., stereotypes, social norms), meaning that they can vary over time and culture and across individuals. Hence, social psychologists have advocated the use of “conceptual replications” that reproduce an experiment by relying on different operationalizations of the concepts under investigation (Stroebe & Strack, 2014). For example, in a society in which old age is associated not with slowness but with, say, talkativeness, the outcome variable could be the number of words uttered by the subject at the end of the experiment rather than walking speed.”

***Welcome back Theory
Ap Dijksterhuis
(ER uninformative)
“it is unavoidable, and indeed, this commentary is also about replication—it is done against the background of something we had almost forgotten: theory! S&S (2014, this issue) argue that focusing on the replication of a phenomenon without any reference to underlying theoretical mechanisms is uninformative”

On the scientific superiority of conceptual replications for scientific progress
Christian S. Crandall, Jeffrey W. Sherman
(ER impossible)
But in matters of social psychology, one can never step in the same river twice—our phenomena rely on culture, language, socially primed knowledge and ideas, political events, the meaning of questions and phrases, and an ever-shifting experience of participant populations (Ramscar, 2015). At a certain level, then, all replications are “conceptual” (Stroebe & Strack, 2014), and the distinction between direct and conceptual replication is continuous rather than categorical (McGrath, 1981). Indeed, many direct replications turn out, in fact, to be conceptual replications. At the same time, it is clear that direct replications are based on an attempt to be as exact as possible, whereas conceptual replications are not.

***Are most published social psychological findings false?
Stroebe, W.
(ER uninformative)
This near doubling of replication success after combining original and replication effects is puzzling. Because these replications were already highly powered, the increase is unlikely to be due to the greater power of a meta-analytic synthesis. The two most likely explanations are quality problems with the replications or publication bias in the original studies or. An evaluation of the quality of the replications is beyond the scope of this review and should be left to the original authors of the replicated studies. However, the fact that all replications were exact rather than conceptual replications of the original studies is likely to account to some extent for the lower replication rate of social psychological studies (Stroebe & Strack, 2014). There is no evidence either to support or to reject the second explanation.”

(ER impossible)
“All four projects relied on exact replications, often using the material used in the original studies. However, as I argued earlier (Stroebe & Strack, 2014), even if an experimental manipulation exactly replicates the one used in the original study, it may not reflect the same theoretical variable.”

(CR test theory)
“Gergen’s argument has important implications for decisions about the appropriateness of conceptual compared to exact replication. The more a phenomenon is susceptible to historical change, the more conceptual replication rather than exact replication becomes appropriate (Stroebe & Strack, 2014).”

(CR test theory)
“Moonesinghe et al. (2007) argued that any true replication should be an exact replication, “a precise processwhere the exact same finding is reexamined in the same way”. However, conceptual replications are often more informative than exact replications, at least in studies that are testing theoretical predictions (Stroebe & Strack, 2014). Because conceptual replications operationalize independent and/or dependent variables in a different way, successful conceptual replications increase our trust in the predictive validity of our theory.”

There’s More Than One Way to Conduct a Replication Study: Beyond Statistical Significance”
Anderson & Maxwell
“It is important to note some caveats regarding direct (exact) versus conceptual replications. While direct replications were once avoided for lack of originality, authors have recently urged the field to take note of the benefits and importance of direct replication. According to Simons (2014), this type of replication is “the only way to verify the reliability of an effect” (p. 76). With respect to this recent emphasis, the current article will assume direct replication. However, despite the push toward direct replication, some have still touted the benefits of conceptual replication (Stroebe & Strack, 2014). Importantly, many of the points and analyses suggested in this paper may translate well to conceptual replication.”

Reconceptualizing replication as a sequence of different studies: A replication typology
Joachim Hüffmeier, Jens Mazei, Thomas Schultze
(ER impossible)
The first type of replication study in our typology encompasses exact replication studies conducted by the author(s) of an original finding. Whereas we must acknowledge that replications can never be “exact” in a literal sense in psychology (Cesario, 2014; Stroebe & Strack, 2014), exact replications are studies that aspire to be comparable to the original study in all aspects (Schmidt, 2009). Exact replications—at least those that are not based on questionable research practices such as the arbitrary exclusion of critical outliers, sampling or reporting biases (John, Loewenstein, & Prelec, 2012; Simmons, Nelson, & Simonsohn, 2011)—serve the function of protecting against false positive effects (Type I errors) right from the start.

(ER informative)
Thus, this replication constitutes a valuable contribution to the research process. In fact, already some time ago, Lykken (1968; see also Mummendey, 2012) recommended that all experiments should be replicated  before publication. From our perspective, this recommendation applies in particular to new findings (i.e., previously uninvestigated theoretical relations), and there seems to be some consensus that new findings should be replicated at least once, especially when they were unexpected, surprising, or only loosely connected to existing theoretical models (Stroebe & Strack, 2014; see also Giner-Sorolla, 2012; Murayama et al., 2014).”

Although there is currently some debate about the epistemological value of close replication studies (e.g., Cesario, 2014; LeBel & Peters, 2011; Pashler & Harris, 2012; Simons, 2014; Stroebe & Strack, 2014), the possibility that each original finding can—in principal—be replicated by the scientific community represents a cornerstone of science (Kuhn, 1962; Popper, 1992).”

(CR test theory)
So far, we have presented “only” the conventional rationale used to stress the importance of close replications. Notably, however, we will now add another—and as we believe, logically necessary—point originally introduced by S&S (2014). This point protects close replications from being criticized (cf. Cesario, 2014; Stroebe & Strack, 2014; see also LeBel & Peters, 2011). Close replications can be informative only as long as they ensure that the theoretical processes investigated or at least invoked by the original study are shown to also operate in the replication study.

(CR test theory)
The question of how to conduct a close replication that is maximally informative entails a number of methodological choices. It is important to both adhere to the original study proceedings (Brandt et al., 2014; Schmidt, 2009) and focus on and meticulously measure the underlying theoretical mechanisms that were shown or at least proposed in the original studies (Stroebe & Strack, 2014). In fact, replication attempts are most informative when they clearly demonstrate either that the theoretical processes have unfolded as expected or at which point in the process the expected results could no longer be observed (e.g., a process ranging from a treatment check to a manipulation check and [consecutive] mediator variables to the dependent variable). Taking these measures is crucial to rule out that a null finding is simply due to unsuccessful manipulations or changes in a manipulation’s meaning and impact over time (cf. Stroebe & Strack, 2014). “

(CR test theory)
Conceptual replications in laboratory settings are the fourth type of replication study in our typology. In these replications, comparability to the original study is aspired to only in the aspects that are deemed theoretically relevant (Schmidt, 2009; Stroebe & Strack, 2014). In fact, most if not all aspects may differ as long as the theoretical processes that have been studied or at least invoked in the original study are also covered in a conceptual replication study in the laboratory.”

(ER useful for applied research)
For instance, conceptual replications may be less important for applied disciplines that focus on clinical phenomena and interventions. Here, it is important to ensure that there is an impact of a specific intervention and that the related procedure does not hurt the members of the target population (e.g., Larzelere et al., 2015; Stroebe & Strack, 2014).”

From intrapsychic to ecological theories in social psychology: Outlines of a functional theory approach
Klaus Fiedler
(ER uninformative)
Replicating an ill-understood finding is like repeating a complex sentence in an unknown language. Such a “replication” in the absence of deep understanding may appear funny, ridiculous, and embarrassing to a native speaker, who has full control over the foreign language. By analogy, blindly replicating or running new experiments on an ill-understood finding will rarely create real progress (cf. Stroebe & Strack, 2014). “

Into the wild: Field research can increase both replicability and real-world impact
Jon K. Maner
(CR test theory)
Although studies relying on homogeneous samples of laboratory or online participants might be highly replicable when conducted again in a similar homogeneous sample of laboratory or online participants, this is not the key criterion (or at least not the only criterion) on which we should judge replicability (Westfall, Judd & Kenny, 2015; see also Brandt et al., 2014; Stroebe & Strack, 2014). Just as important is whether studies replicate in samples that include participants who reflect the larger and more diverse population.”

Romance, Risk, and Replication: Can Consumer Choices and Risk-Taking Be Primed by Mating Motives?
Shanks et al.
(ER impossible)
There is no such thing as an “exact” replication (Stroebe & Strack, 2014) and hence it must be acknowledged that the published studies (notwithstanding the evidence for p-hacking and/or publication bias) may have obtained genuine effects and that undetected moderator variables explain why the present studies failed to obtain priming.   Some of the experiments reported here differed in important ways from those on which they were modeled (although others were closer replications and even these failed to obtain evidence of reliable romantic priming).

(CR test theory)
As S&S (2014) point out, what is crucial is not so much exact surface replication but rather identical operationalization of the theoretically relevant variables. In the present case, the crucial factors are the activation of romantic motives and the appropriate assessment of consumption, risk-taking, and other measures.”

A Duty to Describe: Better the Devil You Know Than the Devil You Don’t
Brown, Sacha D et al.
Ioannidis (2005) has been at the forefront of researchers identifying factors interfering with self-correction. He has claimed that journal editors selectively publish positive findings and discriminate against study replications, permitting errors in data and theory to enjoy a long half-life (see also Ferguson & Brannick, 2012; Ioannidis, 2008, 2012; Shadish, Doherty, & Montgomery, 1989; Stroebe & Strack, 2014). We contend there are other equally important, yet relatively unexplored, problems.

A Room with a Viewpoint Revisited: Descriptive Norms and Hotel Guests’ Towel Reuse Behavior
(Contextual Sensitivity)
Bohner, Gerd; Schlueter, Lena E.
On the other hand, our pilot participants’ estimates of towel reuse rates were generally well below 75%, so we may assume that the guests participating in our experiments did not perceive the normative messages as presenting a surprisingly low figure. In a more general sense, the issue of greatly diverging baselines points to conceptual issues in trying to devise a ‘‘direct’’ replication: Identical operationalizations simply may take on different meanings for people in different cultures.

***The empirical benefits of conceptual rigor: Systematic articulation of conceptual hypotheses can reduce the risk of non-replicable results (and facilitate novel discoveries too)
Mark Schaller
(Contextual Sensitivity)
Unless these subsequent studies employ methods that exactly replicate the idiosyncratic context in which the effect was originally detected, these studies are unlikely to replicate the effect. Indeed, because many psychologically important contextual variables may lie outside the awareness of researchers, even ostensibly “exact” replications may fail to create the conditions necessary for a fragile effect to emerge (Stroebe & Strack, 2014)

A Concise Set of Core Recommendations to Improve the Dependability of Psychological Research
David A. Lishner
(CR test theory)
The claim that direct replication produces more dependable findings across replicated studies than does conceptual replication seems contrary to conventional wisdom that conceptual replication is preferable to direct replication (Dijksterhuis, 2014; Neulip & Crandall, 1990, 1993a, 1993b; Stroebe & Strack, 2014).
(CR test theory)
However, most arguments advocating conceptual replication over direct replication are attempting to promote the advancement or refinement of theoretical understanding (see Dijksterhuis, 2014; Murayama et al., 2014; Stroebe & Strack, 2014). The argument is that successful conceptual replication demonstrates a hypothesis (and by extension the theory from which it derives) is able to make successful predictions even when one alters the sampled population, setting, operations, or data analytic approach. Such an outcome not only suggests the presence of an organizing principle, but also the quality of the constructs linked by the organizing principle (their theoretical meanings). Of course this argument assumes that the consistency across the replicated findings is not an artifact of data acquisition or data analytic approaches that differ among studies. The advantage of direct replication is that regardless of how flexible or creative one is in data acquisition or analysis, the approach is highly similar across replication studies. This duplication ensures that any false finding based on using a flexible approach is unlikely to be repeated multiple times.

(CR test theory)
Does this mean conceptual replication should be abandoned in favor of direct replication? No, absolutely not. Conceptual replication is essential for the theoretical advancement of psychological science (Dijksterhuis, 2014; Murayama et al., 2014; Stroebe & Strack, 2014), but only if dependability in findings via direct replication is first established (Cesario, 2014; Simons, 2014). Interestingly, in instances where one is able to conduct multiple studies for inclusion in a research report, one approach that can produce confidence in both dependability of findings and theoretical generalizability is to employ nested replications.

(ER cannot detect fraud)
A second advantage of direct replications is that they can protect against fraudulent findings (Schmidt, 2009), particularly when different research groups conduct direct replication studies of each other’s research. S&S (2014) make a compelling argument that direct replication is unlikely to prove useful in detection of fraudulent research. However, even if a fraudulent study remains unknown or undetected, its impact on the literature would be lessened when aggregated with nonfraudulent direct replication studies conducted by honest researchers.

***Does cleanliness influence moral judgments? Response effort moderates the effect of cleanliness priming on moral judgments.
(ER uninformative)
Indeed, behavioral priming effects in general have been the subject of increased scrutiny (see Cesario, 2014), and researchers have suggested different causes for failed replication, such as measurement and sampling errors (Stanley and Spence,2014), variation in subject populations (Cesario, 2014), discrepancy in operationalizations (S&S, 2014), and unidentified moderators (Dijksterhuis,2014).

Daniel C. Molden
(ER uninformative)
Therefore, some greater emphasis on direct replication in addition to conceptual replication is likely necessary to maximize what can be learned from further research on priming (but see Stroebe and Strack, 2014, for costs of overemphasizing direct replication as well).

On the automatic link between affect and tendencies to approach and avoid: Chen and Bargh (1999) revisited
Mark Rotteveel et al.
(no replication crisis)
Although opinions differ with regard to the extent of this “replication crisis” (e.g., Pashler and Harris, 2012; S&S, 2014), the scientific community seems to be shifting its focus more toward direct replication.

(ER uninformative)
Direct replications not only affect one’s confidence about the veracity of the phenomenon under study, but they also increase our knowledge about effect size (see also Simons, 2014; but see also S&S, 2014).

Single-Paper Meta-Analysis: Benefits for Study Summary, Theory Testing, and Replicability
McShane and Bockenholt
(ER impossible)
The purpose of meta-analysis is to synthesize a set of studies of a common phenomenon. This task is complicated in behavioral research by the fact that behavioral research studies can never be direct or exact replications of one another (Brandt et al. 2014; Fabrigar and Wegener 2016; Rosenthal 1991; S&S 2014; Tsang and Kwan 1999).

(ER impossible)
Further, because behavioral research studies can never be direct or exact replications of one another (Brandt et al. 2014; Fabrigar and Wegener 2016; Rosenthal 1991; S&S 2014; Tsang and Kwan 1999), our SPM methodology estimates and accounts for heterogeneity, which has been shown to be important in a wide variety of behavioral research settings (Hedges and Pigott 2001; Klein et al. 2014; Pigott 2012).

A Closer Look at Social Psychologists’ Silver Bullet: Inevitable and Evitable Side   Effects of the Experimental Approach
Herbert Bless and Axel M. Burger
(ER/CR Distinction)
Given the above perspective, it becomes obvious that in the long run, conceptual replications can provide very fruitful answers because they address the question of whether the initially observed effects are potentially caused by some perhaps unknown aspects of the experimental procedure (for a discussion of conceptual versus direct replications, see e.g., Stroebe & Strack, 2014; see also Brandt et al., 2014; Cesario, 2014; Lykken, 1968; Schwarz & Strack, 2014).  Whereas conceptual replications are adequate solutions for broadening the sample of situations (for examples, see Stroebe & Strack, 2014), the present perspective, in addition, emphasizes that it is important that the different conceptual replications do not share too much overlap in general aspects of the experiment (see also Schwartz, 2015, advocating for  conceptual replications)

Men in red: A reexamination of the red-attractiveness effect
Vera M. Hesslinger, Lisa Goldbach, & Claus-Christian Carbon
(ER impossible)
As Brandt et al. (2014) pointed out, a replication in psychological research will never be absolutely exact or direct (see also, Stroebe & Strack, 2014), which is, of course, also the case in the present research.

***On the challenges of drawing conclusions from p-values just below 0.05
Daniel Lakens
(no evidence about QRP)
In recent years, researchers have become more aware of how flexibility during the data-analysis can increase false positive results (e.g., Simmons, Nelson & Simonsohn, 2011). If the true Type 1 error rate is substantially inflated, for example because researchers analyze their data until a p-value smaller than 0.05 is observed, the robustness of scientific knowledge can substantially decrease. However, as Stroebe & Strack (2014, p. 60) have pointed out: ‘Thus far, however, no solid data exist on the prevalence of such research practices.’

***Does Merely Going Through the Same Moves Make for a ‘‘Direct’’ Replication? Concepts, Contexts, and Operationalizations
Norbert Schwarz and Fritz Strack
(Contextual Sensitivity)
In general, meaningful replications need to realize the psychological conditions of the original study. The easier option of merely running through technically identical procedures implies the assumption that psychological processes are context insensitive and independent of social, cultural, and historical differences (Cesario, 2014; Stroebe & Strack, 2014). Few social (let alone cross-cultural) psychologists would be willing to endorse this assumption with a straight face. If so, mere procedural equivalence is an insufficient criterion for assessing the quality of a replication.

The Replication Paradox: Combining Studies can Decrease Accuracy of Effect Size Estimates
(ER uninformative)
Michèle B. Nuijten, Marcel A. L. M. van Assen, Coosje L. S. Veldkamp, and Jelte M. Wicherts
Replications with nonsignificant results are easily dismissed with the argument that the replication might contain a confound that caused the null finding (Stroebe & Strack, 2014).

Retro-priming, priming, and double testing: psi and replication in a test-retest design
Rabeyron, T
Bem’s paper spawned numerous attempts to replicate it (see e.g., Galak et al., 2012; Bem et al., submitted) and reflections on the difficulty of direct replications in psychology (Ritchie et al., 2012). This aspect has been associated more generally with debates concerning the “decline effect” in science (Schooler, 2011) and a potential “replication crisis” (S&S, 2014) especially in the fields of psychology and medical sciences (De Winter and Happee, 2013).

Do p Values Lose Their Meaning in Exploratory Analyses? It Depends How You Define the Familywise Error Rate
Mark Rubin
(ER impossible)
Consequently, the Type I error rate remains constant if researchers simply repeat the same test over and over again using different samples that have been randomly drawn from the exact same population. However, this first situation is somewhat hypothetical and may even be regarded as impossible in the social sciences because populations of people change over time and location (e.g., Gergen, 1973; Iso-Ahola, 2017; Schneider, 2015; Serlin, 1987; Stroebe & Strack, 2014). Yesterday’s population of psychology undergraduate students from the University of Newcastle, Australia, will be a different population to today’s population of psychology undergraduate students from the University of Newcastle, Australia.

***Learning and the replicability of priming effects
Michael Ramscar
(ER uninformative)
In the limit, this means that in the absence of a means for objectively determining what the information that produces a priming effect is, and for determining that the same information is available to the population in a replication, all learned priming effects are scientifically unfalsifiable. (Which also means that in the absence of an account of what the relevant information is in a set of primes, and how it produces a specific effect, reports of a specific priming result — or failures to replicate it — are scientifically uninformative; see also [Stroebe & Strack, 2014.)

***Evaluating Psychological Research Requires More Than Attention to the N: A Comment on Simonsohn’s (2015) “Small Telescopes”
Norbert Schwarz and Gerald L. Clore
(CR test theory)
Simonsohn’s decision to equate a conceptual variable (mood) with its manipulation (weather) is compatible with the logic of clinical trials, but not with the logic of theory testing. In clinical trials, which have inspired much of the replicability debate and its statistical focus, the operationalization (e.g., 10 mg of a drug) is itself the variable of interest; in theory testing, any given operationalization is merely one, usually imperfect, way to realize the conceptual variable. For this reason, theory tests are more compelling when the results of different operationalizations converge (Stroebe & Strack, 2014), thus ensuring, in the case in point, that it is not “the weather” but indeed participants’ (sometimes weather-induced) mood that drives the observed effect.

Internal conceptual replications do not increase independent replication success
Kunert, R
(Contextual Sensitivity)
According to the unknown moderator account of independent replication failure, successful internal replications should correlate with independent replication success. This account suggests that replication failure is due to the fact that psychological phenomena are highly context-dependent, and replicating seemingly irrelevant contexts (i.e. unknown moderators) is rare (e.g., Barrett, 2015; DGPS, 2015; Fleming Crim, 2015; see also Stroebe & Strack, 2014; for a critique, see Simons, 2014). For example, some psychological phenomenon may unknowingly be dependent on time of day.

(Contextual Sensitivity greater in social psychology)
When the chances of unknown moderator influences are greater and replicability is achieved (internal, conceptual replications), then the same should be true when chances are smaller (independent, direct replications). Second, the unknown moderator account is usually invoked for social psychological effects (e.g. Cesario, 2014; Stroebe & Strack, 2014). However, the lack of influence of internal replications on independent replication success is not limited to social psychology. Even for cognitive psychology a similar pattern appears to hold.

On Klatzky and Creswell (2014): Saving Social Priming Effects But Losing Science as We Know It?
Barry Schwartz
(ER uninformative)
The recent controversy over what counts as “replication” illustrates the power of this presumption. Does “conceptual replication” count? In one respect, conceptual replication is a real advance, as conceptual replication extends the generality of the phenomena that were initially discovered. But what if it fails? Is it because the phenomena are unreliable, because the conceptual equivalency that justified the new study was logically flawed, or because the conceptual replication has permitted the intrusion of extraneous variables that obscure the original phenomenon? This ambiguity has led some to argue that there is no substitute for strict replication (see Pashler & Harris, 2012; Simons, 2014, and Stroebe & Strack, 2014, for recent manifestations of this controversy). A significant reason for this view, however, is less a critique of the logic of conceptual replication than it is a comment on the sociology (or politics, or economics) of science. As Pashler and Harris (2012) point out, publication bias virtually guarantees that successful conceptual replications will be published whereas failed conceptual replications will live out their lives in a file drawer.  I think Pashler and Harris’ surmise is probably correct, but it is not an argument for strict replication so much as it is an argument for publication of failed conceptual replication.

Commentary and Rejoinder on Lynott et al. (2014)
Lawrence E. Williams
(CR test theory)
On the basis of their investigations, Lynott and colleagues (2014) conclude ‘‘there is no evidence that brief exposure to warm therapeutic packs induces greater prosocial responding than exposure to cold therapeutic packs’’ (p. 219). This conclusion, however, does not take into account other related data speaking to the connection between physical warmth and prosociality. There is a fuller body of evidence to be considered, in which both direct and conceptual replications are instructive. The former are useful if researchers particularly care about the validity of a specific phenomenon; the latter are useful if researchers particularly care about theory testing (Stroebe & Strack, 2014).

The State of Social and Personality Science: Rotten to the Core, Not So Bad, Getting Better, or Getting Worse?
(no replication crisis)
Motyl et al. (2017) “The claim of a replicability crisis is greatly exaggerated.” Wolfgang Stroebe and Fritz Strack, 2014

Promise, peril, and perspective: Addressing concerns about reproducibility in social–personality psychology
Harry T. Reis, Karisa Y. Lee
(ER impossible)
Much of the current debate, however, is focused narrowly on direct or exact replications—whether the findings of a given study, carried out in a particular way with certain specific operations, would be repeated. Although exact replications are surely desirable, the papers by Fabrigar and by Crandall and Sherman remind us that in an absolute sense they are fundamentally impossible in social–personality psychology (see also S&S, 2014).

Show me the money
(Contextual Sensitivity)
Of course, it is possible that additional factors, which varied or could have varied among our studies and previously published studies (e.g., participants’ attitudes toward money) or among the online studies and laboratory study in this article (e.g., participants’ level of distraction), might account for these apparent inconsistencies. We did not aim to conduct a direct replication of any specific past study, and therefore we encourage special care when using our findings to evaluate existing ones (Doyen, Klein, Simons, & Cleeremans, 2014; Stroebe & Strack, 2014).

***From Data to Truth in Psychological Science. A Personal Perspective.
(ER uninformative)
In their introduction to the 2016 volume of the Annual Review of Psychology, Susan Fiske, Dan Schacter, and Shelley Taylor point out that a replication failure is not a scientific problem but an opportunity to find limiting conditions and contextual effects. To allow non-replications to regain this constructive role, they must come with conclusions that enter and stimulate a critical debate. It is even better if replication studies are endowed with a hypothesis that relates to the state of the scientific discourse. To show that an effect occurs only under one but not under another condition is more informative than simply demonstrating noneffects (S&S, 2014). But this may require expertise and effort.


Replicability 101: How to interpret the results of replication studies

Even statistically sophisticated psychologists struggle with the interpretation of replication studies (Maxwell et al., 2015).  This article gives a basic introduction to the interpretation of statistical results within the Neyman Pearson approach to statistical inferences.

I make two important points and correct some potential misunderstandings in Maxwell et al.’s discussion of replication failures.  First, there is a difference between providing sufficient evidence for the null-hypothesis (evidence of absence) and providing insufficient evidence against the null-hypothesis (absence of evidence).  Replication studies are useful even if they simply produce absence of evidence without evidence that an effect is absent.  Second, I  point out that publication bias undermines the credibility of significant results in original studies.  When publication bias is present, open replication studies are valuable because they provide an unbiased test of the null-hypothesis, while original studies are rigged to reject the null-hypothesis.


Replicating something means to get the same result.  If I make the first free throw, replicating this outcome means to also make the second free throw.  When we talk about replication studies in psychology we borrow from the common meaning of the term “to replicate.”

If we conduct psychological studies, we can control many factors, but some factors are not under our control.  Participants in two independent studies differ from each other and the variation in the dependent variable across samples introduces sampling error. Hence, it is practically impossible to get identical results, even if the two studies are exact copies of each other.  It is therefore more complicated to compare the results of two studies than to compare the outcome of two free throws.

To determine whether the results of two studies are identical or not, we need to focus on the outcome of a study.  The most common outcome in psychological studies is a significant or non-significant result.  The goal of a study is to produce a significant result and for this reason a significant result is often called a success.  A successful replication study is a study that also produces a significant result.  Obtaining two significant results is akin to making two free throws.  This is one of the few agreements between Maxwell and me.

“Generally speaking, a published  original study has in all likelihood demonstrated a statistically significant effect. In the current zeitgeist, a replication study is usually interpreted as successful if it also demonstrates a statistically significant effect.” (p. 488)

The more interesting and controversial scenario is a replication failure. That is, the original study produced a significant result (success) and the replication study produced a non-significant result (failure).

I propose that a lot of confusion arises from the distinction between original and replication studies. If a replication study is an exact copy of the first study, the outcome probabilities of original and replication studies are identical.  Otherwise, the replication study is not really a replication study.

There are only three possible outcomes in a set of two studies: (a) both studies are successful, (b) one study is a success and one is a failure, or (c) both studies are failures.  The probability of these outcomes depends on whether the significance criterion (the type-I error probability) when the null-hypothesis is true and the statistical power of a study when the null-hypothesis is false.

Table 1 shows the probability of the outcomes in two studies.  The uncontroversial scenario of two significant results is very unlikely, if the null-hypothesis is true. With conventional alpha = .05, the probability is .0025 or 1 out of 400 attempts.  This shows the value of replication studies. False positives are unlikely to repeat themselves and a series of replication studies with significant results is unlikely to occur by chance alone.

2 sig, 0 ns 1 sig, 1 ns 0 sig, 2 ns
H0 is True alpha^2 2*alpha*(1-alpha) (1-alpha^2)
H1 is True (1-beta)^2 2*(1-beta)*beta beta^2

The probability of a successful replication of a true effect is a function of statistical power (1 – type-II error probability).  High power is needed to get significant results in a pair of studies (an original study and a replication study).  For example, if power is only 50%, the chance of this outcome is only 25% (Schimmack, 2012).  Even with conventionally acceptable power of 80%, only 2/3 (64%) of replication attempts would produce this outcome.  However, studies in psychology do not have 80% power and estimates of power can be as low as 37% (OSC, 2015). With 40% power, a pair of studies would produce significant results in no more than 16 out of 100 attempts.   Although successful replications of true effects with low power are unlikely, they are still much more likely then significant results when the null-hypothesis is true (16/100 vs. 1/400 = 64:1).  It is therefore reasonable to infer from two significant results that the null-hypothesis is false.

If the null-hypothesis is true, it is extremely likely that both studies produce a non-significant result (.95^2 = 90.25%).  In contrast, it is unlikely that even a study with modest power would produce two non-significant results.  For example, if power is 50%, there is a 75% chance that at least one of the two studies produces a significant result. If power is 80%, the probability of obtaining two non-significant results is only 4%.  This means, it is much more likely (22.5 : 1) that the null-hypothesis is true than that the alternative hypothesis is true.  This does not mean that the null-hypothesis is true in an absolute sense because power depends on the effect size.  For example, if 80% power were obtained with a standardized effect size of Cohen’s d = .5,  two non-significant results would suggest that the effect size is smaller than .5, but it does not warrant the conclusion that H0 is true and the effect size is exactly 0.  Once more, it is important to distinguish between the absence of evidence for an effect and the evidence of absence of an effect.

The most controversial scenario assumes that the two studies produced inconsistent outcomes.  Although theoretically there is no difference between the first and the second study, it is common to focus on a successful outcome followed by a replication failure  (Maxwell et al., 2015). When the null-hypothesis is true, the probability of this outcome is low;  .05 * (1-.05) = .0425.  The same probability exists for the reverse pattern that a non-significant result is followed by a significant one.  A probability of 4.25% shows that it is unlikely to observe a significant result followed by a non-significant result when the null-hypothesis is true. However, the low probability is mostly due to the low probability of obtaining a significant result in the first study, while the replication failure is extremely likely.

Although inconsistent results are unlikely when the null-hypothesis is true, they can also be unlikely when the null-hypothesis is false.  The probability of this outcome depends on statistical power.  A pair of studies with very high power (95%) is very unlikely to produce an inconsistent outcome because both studies are expected to produce a significant result.  The probability of this rare event can be as low, or lower, than the probability with a true null effect; .95 * (1-.95) = .0425.  Thus, an inconsistent result provides little information about the probability of a type-I or type-II  error and is difficult to interpret.

In conclusion, a pair of significance tests can produce three outcomes. All three outcomes can occur when the null-hypothesis is true and when it is false.  Inconsistent outcomes are likely unless the null-hypothesis is true or the null-hypothesis is false and power is very high.  When two studies produce inconsistent results, statistical significance provides no basis for statistical inferences.


The counting of successes and failures is an old way to integrate information from multiple studies.  This approach has low power and is no longer used.  A more powerful approach is effect size meta-analysis.  Effect size meta-analysis was one way to interpret replication results in the Open Science Collaboration (2015) reproducibility project.  Surprisingly, Maxwell et al. (2015) do not consider this approach to the interpretation of failed replication studies. To be clear, Maxwell et al. (2015) mention meta-analysis, but they are talking about meta-analyzing a larger set of replication studies, rather than meta-analyzing the results of an original and a replication study.

“This raises a question about how to analyze the data obtained from multiple studies. The natural answer is to use meta-analysis.” (p. 495)

I am going to show that effect-size meta-analysis solves the problem of interpreting inconsistent results in pairs of studies. Importantly, effect size meta-analysis does not care about significance in individual studies.  A meta-analysis of a pair of studies with inconsistent results is no different from a meta-analysis of a pair of studies with consistent results.

Maxwell et al.’s (2015) introduced an example of a between-subject (BS) design with n = 40 per group (total N = 80) and a standardized effect size of Cohen’s d = .5 (a medium effect size).  This study has 59% power to obtain a significant result.  Thus, it is quite likely that a pair of studies produces inconsistent results (48.38%).   However, a pair of studies with N = 80 has the power of a total sample size of N = 160, which means a fixed-effects meta-analysis will produce a significant result in 88% of all attempts.  Thus, it is not difficult at all to interpret the results of pairs of studies with inconsistent results if the studies have acceptable power (> 50%).   Even if the results are inconsistent, a meta-analysis will provide the correct answer that there is an effect most of the time.

A more interesting scenario are inconsistent results when the null-hypothesis is true.  I turned to simulations to examine this scenario more closely.   The simulation showed that a meta-analysis of inconsistent studies produced a significant result in 34% of all cases.  The percentage slightly varies as a function of sample size.  With a small sample of N = 40, the percentage is 35%. With a large sample of  1,000 participants it is 33%.  This finding shows that in two-thirds of attempts, a failed replication reverses the inference about the null-hypothesis based on a significant original study.  Thus, if an original study produced a false-positive results, a failed replication study corrects this error in 2 out of 3 cases.  Importantly, this finding does not warrant the conclusion that the null-hypothesis is true. It merely reverses the result of the original study that falsely rejected the null-hypothesis.

In conclusion, meta-analysis of effect sizes is a powerful tool to interpret the results of replication studies, especially failed replication studies.  If the null-hypothesis is true, failed replication studies can reduce false positives by 66%.


We can all agree that, everything else being equal, larger samples are better than smaller samples (Cohen, 1990).  This rule applies equally to original and replication studies. Sometimes it is recommended that replication studies should use much larger samples than original studies, but it is not clear to me why researchers who conduct replication studies should have to invest more resources than original researchers.  If original researchers conducted studies with adequate power,  an exact replication study with the same sample size would also have adequate power.  If the original study was a type-I error, the replication study is unlikely to replicate the result no matter what the sample size.  As demonstrated above, even a replication study with the same sample size as the original study can be effective in reversing false rejections of the null-hypothesis.

From a meta-analytic perspective, it does not matter whether a replication study had a larger or smaller sample size.  Studies with larger sample sizes are given more weight than studies with smaller samples.  Thus, researchers who invest more resources are rewarded by giving their studies more weight.  Large original studies require large replication studies to reverse false inferences, whereas small original studies require only small replication studies to do the same.  Nevertheless, failed replications with larger samples are more likely to reverse false rejections of the null-hypothesis, but there is no magical number about the size of a replication study to be useful.

I simulated a scenario with a sample size of N = 80 in the original study and a sample size of N = 200 in the replication study (a factor of 2.5).  In this simulation, only 21% of meta-analyses produced a significant result.  This is 13 percentage points lower than in the simulation with equal sample sizes (34%).  If the sample size of the replication study is 10 times larger (N = 80 and N = 800), the percentage of remaining false positive results in the meta-analysis shrinks to 10%.

The main conclusion is that even replication studies with the same sample size as the original study have value and can help to reverse false positive findings.  Larger sample sizes simply give replication studies more weight than original studies, but it is by no means necessary to increase sample sizes of replication studies to make replication failures meaningful.  Given unlimited resources, larger replications are better, but these analysis show that large replication studies are not necessary.  A replication study with the same sample size as the original study is more valuable than no replication study at all.


One problem in Maxwell et al’s (2015) article is to conflate two possible goals of replication studies.  One goal is to probe the robustness of the evidence against the null-hypothesis. If the original result was a false positive result, an unsuccessful replication study can reverse the initial inference and produce a non-significant result in a meta-analysis.  This finding would mean that evidence for an effect is absent.  The status of a hypothesis (e.g., humans have supernatural abilities; Bem, 2011) is back to where it was before the original study found a significant result and the burden of proof is shifted back to proponents of the hypothesis to provide unbiased credible evidence for it.

Another goal of replication studies can be to provide conclusive evidence that an original study reported a false positive result (i..e, humans do not have supernatural abilities).  Throughout their article, Maxwell et al. assume that the goal of replication studies is to prove the absence of an effect.  They make many correct observations about the difficulties of achieving this goal, but it is not clear why replication studies have to be conclusive when original studies are not held to the same standard.

This makes it easy to produce (potentially false) positive results and very hard to remove false positive results from the literature.   It also creates a perverse incentive to conduct underpowered original studies and to claim victory when a large replication study finds a significant result with an effect size that is 90% smaller than the effect size in an original study.  The authors of the original article may claim that they do not care about effect sizes and that their theoretical claim was supported.  To avoid this problem that replication researchers have to invest large amount of resources for little gain, it is important to realize that even a failure to replicate an original finding with the same sample size can undermine original claims and force researchers to provide stronger evidence for their original ideas in original articles.  If they are right and the evidence is strong, others will be able to replicate the result in an exact replication study with the same sample size.


The main problem of Maxwell et al.’s (2015) article is that the authors blissfully ignore the problem of publication bias.  They mention publication bias twice to warn readers that publication bias inflates effect sizes and biases power analyses, but they completely ignore the influence of publication bias on the credibility of successful original results (Schimmack, 2012; Sterling; 1959; Sterling et al., 1995).

It is hard to believe that Maxwell is unaware of this problem, if only because Maxwell was action editor of my article that demonstrated how publication bias undermines the credibility of replication studies that are selected for significance  (Schimmack, 2012).

I used Bem’s infamous article on supernatural abilities as an example, which appeared to show 8 successful replications of supernatural abilities.  Ironically, Maxwell et al. (2015) also cites Bem’s article to argue that failed replication studies can be misinterpreted as evidence of absence of an effect.

“Similarly, Ritchie, Wiseman, and French (2012) state that their failure to obtain significant results in attempting to replicate Bem (2011) “leads us to favor the ‘experimental artifacts’ explanation for Bem’s original result” (p. 4)”

This quote is not only an insult to Ritchie et al.; it also ignores the concerns that have been raised about Bem’s research practices. First, Ritchie et al. do not claim that they have provided conclusive evidence against ESP.  They merely express their own opinion that they “favor the ‘experimental artifacts’ explanation.  There is nothing wrong with this statement, even if it is grounded in a healthy skepticism about supernatural abilities.

More important, Maxwell et al. ignore the broader context of these studies.  Schimmack (2012) discussed many questionable practices in Bem’s original studies and I presented statistical evidence that the significant results in Bem’s article were obtained with the help of questionable research practices.  Given this wider context, it is entirely reasonable to favor the experimental artifact explanation over the alternative hypothesis that learning after an exam can still alter the exam outcome.

It is not clear why Maxwell et al. (2015) picked Bem’s article to discuss problems with failed replication studies and ignores that questionable research practices undermine the credibility of significant results in original research articles. One reason why failed replication studies are so credible is that insiders know how incredible some original findings are.

Maxwell et al. (2015) were not aware that in the same year, the OSC (2015) reproducibilty project would replicate only 37% of statistically significant results in top psychology journals, while the apparent success rate in these journals is over 90%.  The stark contrast between the apparent success rate and the true power to produce successful outcomes in original studies provided strong evidence that psychology is suffering from a replication crisis. This does not mean that all failed replications are false positives, but it does mean that it is not clear which findings are false positives and which findings are not.  Whether this makes things better is a matter of opinion.

Publication bias also undermines the usefulness of meta-analysis for hypothesis testing.  In the OSC reproducibility project, a meta-analysis of original and replication studies produced 68% significant results.  This result is meaningless because publication bias inflates effect sizes and the probability of obtaining a false positive result in the meta-analysis. Thus, when publication bias is present, unbiased replication studies provide the most credible evidence and the large number of replication failures means that more replication studies with larger samples are needed to see which hypothesis predict real effects with practical significance.


Maxwell et al.’s (2015) answer to this question is captured in this sentence. “Despite raising doubts about the extent to which apparent failures to replicate necessarily reveal that psychology is in crisis,we do not intend to dismiss concerns about documented methodological flaws in the field.” (p. 496).  The most important part of this quote is “raising doubt,” the rest is Orwellian double-talk.

The whole point of Maxwell et al.’s article is to assure fellow psychologists that psychology is not in crisis and that failed replication studies should not be a major concern.  As I have pointed out, this conclusion is based on some misconceptions about the purpose of replication studies and by blissful ignorance about publication bias and questionable research practices that made it possible to publish successful replications of supernatural phenomena, while discrediting authors who spend time and resources on demonstrating that unbiased replication studies fail.

The real answer to Maxwell et al.’s question was provided by the OSC (2015) finding that only 37% of published significant results could be replicated.  In my opinion that is not only a crisis, but a scandal because psychologists routinely apply for funding with power analyses that claim 80% power.  The reproducibilty project shows that the true power to obtain significant results in original and replication studies is much lower than this and that the 90% success rate is no more meaningful than 90% votes for a candidate in communist elections.

In the end, Maxwell et al. draw the misleading conclusion that “the proper design and interpretation of replication studies is less straightforward than conventional practice would suggest.”  They suggest that “most importantly, the mere fact that a replication study yields a nonsignificant statistical result should not by itself lead to a conclusion that the corresponding original study was somehow deficient and should no longer be trusted.”

As I have demonstrated, this is exactly the conclusion that readers should draw from failed replication studies, especially if (a) the original study was not preregistered, (b) the original study produced weak evidence (e.g., p = .04), the original study was published in a journal that only publishes significant results, (d) the replication study had a larger sample, (e) the replication study would have been published independent of outcome, and (f) the replication study was preregistered.

We can only speculate why the American Psychologists published a flawed and misleading article that gives original studies the benefit of the doubt and casts doubt on the value of replication studies when they fail.  Fortunately, APA can no longer control what is published because scientists can avoid the censorship of peer-reviewed journals by publishing blogs and by criticize peer-reviewed articles in open post-publication peer review on social media.

Long life the replicability revolution.  !!!


Cohen, J. (1990). Things I have learned (so far). American Psychologist, 45(12), 1304-1312.

Maxwell, S.E, Lau, M. Y., & Howard, G. S. (2015). Is psychology suffering from a replication crisis? What does ‘failure to replicate’ really mean? American Psychologist, 70, 487-498.

Schimmack, U. (2012). The ironic effect of significant results on the credibility of multiple-study articles. Psychological Methods, 17(4), 551-566.






















What would Cohen say? A comment on p < .005

Most psychologists are trained in Fisherian statistics, which has become known as Null-Hypothesis Significance Testing (NHST).  NHST compares an observed effect size against a hypothetical effect size. The hypothetical effect size is typically zero; that is, the hypothesis is that there is no effect.  The deviation of the observed effect size from zero relative to the amount of sampling error provides a test statistic (test statistic = effect size / sampling error).  The test statistic can then be compared to a criterion value. The criterion value is typically chosen so that only 5% of test statistics would exceed the criterion value by chance alone.  If the test statistic exceeds this value, the null-hypothesis is rejected in favor of the inference that an effect greater than zero was present.

One major problem of NHST is that non-significant results are not considered.  To address this limitation, Neyman and Pearson extended Fisherian statistic and introduced the concepts of type-I (alpha) and type-II (beta) errors.  A type-I error occurs when researchers falsely reject a true null-hypothesis; that is, they infer from a significant result that an effect was present, when there is actually no effect.  The type-I error rate is fixed by the criterion for significance, which is typically p < .05.  This means, that a set of studies cannot produce more than 5% false-positive results.  The maximum of 5% false positive results would only be observed if all studies have no effect. In this case, we would expect 5% significant results and 95% non-significant results.

The important contribution by Neyman and Pearson was to consider the complementary type-II error.  A type-II error occurs when an effect is present, but a study produces a non-significant result.  In this case, researchers fail to detect a true effect.  The type-II error rate depends on the size of the effect and the amount of sampling error.  If effect sizes are small and sampling error is large, test statistics will often be too small to exceed the criterion value.

Neyman-Pearson statistics was popularized in psychology by Jacob Cohen.  In 1962, Cohen examined effect sizes and sample sizes (as a proxy for sampling error) in the Journal of Abnormal and Social Psychology and concluded that there is a high risk of type-II errors because sample sizes are too small to detect even moderate effect sizes and inadequate to detect small effect sizes.  Over the next decades, methodologists have repeatedly pointed out that psychologists often conduct studies with a high risk to fail; that is, to provide empirical evidence for real effects (Sedlemeier & Gigerenzer, 1989).

The concern about type-II errors has been largely ignored by empirical psychologists.  One possible reason is that journals had no problem filling volumes with significant results, while rejecting 80% of submissions that also presented significant results.  Apparently, type-II errors were much less common than methodologists feared.

However, in 2011 it became apparent that the high success rate in journals was illusory. Published results were not representative of studies that were conducted. Instead, researchers used questionable research practices or simply did not report studies with non-significant results.  In other words, the type-II error rate was as high as methodologists suspected, but selection of significant results created the impression that nearly all studies were successful in producing significant results.  The influential “False Positive Psychology” article suggested that it is very easy to produce significant results without an actual effect.  This led to the fear that many published results in psychology may be false positive results.

Doubt about the replicability and credibility of published results has led to numerous recommendations for the improvement of psychological science.  One of the most obvious recommendations is to ensure that published results are representative of the studies that are actually being conducted.  Given the high type-II error rates, this would mean that journals would be filled with many non-significant and inconclusive results.  This is not a very attractive solution because it is not clear what the scientific community can learn from an inconclusive result.  A better solution would be to increase the statistical power of studies. Statistical power is simply the inverse of a type-II error (power = 1 – beta).  As power increases, studies with a true effect have a higher chance of producing a true positive result (e.g., a drug is an effective treatment for a disease). Numerous articles have suggested that researchers should increase power to increase replicability and credibility of published results (e.g., Schimmack, 2012).

In a recent article, a team of 72 authors proposed another solution. They recommended that psychologists should reduce the probability of a type-I error from 5% (1 out of 20 studies) to 0.5% (1 out of 200 studies).  This recommendation is based on the belief that the replication crisis in psychology reflects a large number of type-I errors.  By reducing the alpha criterion, the rate of type-I errors will be reduced from a maximum of 10 out of 200 studies to 1 out of 200 studies.

I believe that this recommendation is misguided because it ignores the consequences of a more stringent significance criterion on type-II errors.  Keeping resources and sampling error constant, reducing the type-I error rate increases the type-II error rate. This is undesirable because the actual type-II error is already large.

For example, a between-subject comparison of two means with a standardized effect size of d = .4 and a sample size of N = 100 (n = 50 per cell) has a 50% risk of a type-II error.  The risk of a type-II error rises to 80%, if alpha is reduced to .005.  It makes no sense to conduct a study with an 80% chance of failure (Tversky & Kahneman, 1971).  Thus, the call for a lower alpha implies that researchers will have to invest more resources to discover true positive results.  Many researchers may simply lack the resources to meet this stringent significance criterion.

My suggestion is exactly opposite to the recommendation of a more stringent criterion.  The main problem for selection bias in journals is that even the existing criterion of p < .05 is too stringent and leads to a high percentage of type-II errors that cannot be published.  This has produced the replication crisis with large file-drawers of studies with p-values greater than .05,  the use of questionable research practices, and publications of inflated effect sizes that cannot be replicated.

To avoid this problem, researchers should use a significance criterion that balances the risk of a type-I and type-II error.  For example, in a between-subject design with an expected effect size of d = .4 and N = 100, researchers should use p < .20 for significance, which reduces the risk of a type -II error to 20%.  In this case, type-I and type-II error are balanced.  If the study produces a p-value of, say, .15, researchers can publish the result with the conclusion that the study provided evidence for the effect. At the same time, readers are warned that they should not interpret this result as strong evidence for the effect because there is a 20% probability of a type-I error.

Given this positive result, researchers can then follow up their initial study with a larger replication study that allows for a stricter type-I error control, while holding power constant.   With d = 4, they now need N = 200 participants to have 80% power and alpha = .05.  Even if the second study does not produce a significant result (the probability that two studies with 80% power are significant is only 64%, Schimmack, 2012), researchers can combine the results of both studies and with N = 300, the combined studies have 80% power with alpha = .01.

The advantage of starting with smaller studies with a higher alpha criterion is that researchers are able to test risky hypothesis with a smaller amount of resources.  In the example, the first study used “only” 100 participants.  In contrast, the proposal to require p < .005 as evidence for an original, risky study implies that researchers need to invest a lot of resources in a risky study that may provide inconclusive results if it fails to produce a significant result.  A power analysis shows that a sample size of N = 338 participants is needed to have 80% power for an effect size of d = .4 and p < .005 as criterion for significance.

Rather than investing 300 participants into a risky study that may produce a non-significant and uninteresting result (eating green jelly beans does not cure cancer), researchers may be better able and willing to start with 100 participants and to follow up an encouraging result with a larger follow-up study.  The evidential value that arises from one study with 300 participants or two studies with 100 and 200 participants is the same, but requiring p < .005 from the start discourages risky studies and puts even more pressure on researchers to produce significant results if all of their resources are used for a single study.  In contrast, lowering alpha reduces the need for questionable research practices and reduces the risk of type-II errors.

In conclusion, it is time to learn Neyman-Pearson statistic and to remember Cohen’s important contribution that many studies in psychology are underpowered.  Low power produces inconclusive results that are not worthwhile publishing.  A study with low power is like a high-jumper that puts the bar too high and fails every time. We learned nothing about the jumpers’ ability. Scientists may learn from high-jump contests where jumpers start with lower and realistic heights and then raise the bar when they succeeded.  In the same manner, researchers should conduct pilot studies or risky exploratory studies with small samples and a high type-I error probability and lower the alpha criterion gradually if the results are encouraging, while maintaining a reasonably low type-II error.

Evidently, a significant result with alpha = .20 does not provide conclusive evidence for an effect.  However, the arbitrary p < .005 criterion also fails short of demonstrating conclusively that an effect exists.  Journals publish thousands of results a year and some of these results may be false positives, even if the error rate is set at 1 out of 200. Thus, p < .005 is neither defensible as a criterion for a first exploratory study, nor conclusive evidence for an effect.  A better criterion for conclusive evidence is that an effect can be replicated across different laboratories and a type-I error probability of less than 1 out of a billion (6 sigma).  This is by no means an unrealistic target.  To achieve this criterion with an effect size of d = .4, a sample size of N = 1,000 is needed.  The combined evidence of 5 labs with N = 200 per lab would be sufficient to produce conclusive evidence for an effect, but only if there is no selection bias.  Thus, the best way to increase the credibility of psychological science is to conduct studies with high power and to minimize selection bias.

This is what I believe Cohen would have said, but even if I am wrong about this, I think it follows from his futile efforts to teach psychologists about type-II errors and statistical power.