Tag Archives: Power

Dr. R’s comment on the Official Statement by the Board of the German Psychological Association (DGPs) about the Results of the OSF-Reproducibility Project published in Science.

Thanks to social media, geography is no longer a barrier for scientific discourse. However, language is still a barrier. Fortunately, I understand German and I can respond to the official statement of the board of the German Psychological Association (DGPs), which was posted on the DGPs website (in German).

BACKGROUND

On September 1, 2015, Prof. Dr. Andrea Abele-Brehm, Prof. Dr. Mario Gollwitzer, and Prof. Dr. Fritz Strack published an official response to the results of the OSF-Replication Project – Psychology (in German) that was distributed to public media in order to correct potentially negative impressions about psychology as a science.

Numerous members of DGPs felt that this official statement did not express their views and noticed that members were not consulted about the official response of their organization. In response to this criticism, DGfP opened a moderated discussion page, where members could post their personal views (mostly in German).

On October 6, 2015, the board closed the discussion page and posted some final words (Schlussbeitrag). In this blog, I provide a critical commentary on these final words.

BOARD’S RESPONSE TO COMMENTS

The board members provide a summary of the core insights and arguments of the discussion from their (personal/official) perspective.

„Wir möchten nun die aus unserer Sicht zentralen Erkenntnisse und Argumente der unterschiedlichen Forumsbeiträge im Folgenden zusammenfassen und deutlich machen, welche vorläufigen Erkenntnisse wir im Vorstand aus ihnen ziehen.“

1. 68% success rate?

The first official statement suggested that the replication project showed that 68% of studies. This number is based on significance in a meta-analysis of the original and replication study. Critics pointed out that this approach is problematic because the replication project showed clearly that the original effect sizes were inflated (on average by 100%). Thus, the meta-analysis is biased and the 68% number is inflated.

In response to this criticism, the DGPs board states that “68% is the maximum [größtmöglich] optimistic estimate.” I think the term “biased and statistically flawed estimate” is a more accurate description of this estimate.   It is common practice to consider fail-safe-N or to correct meta-analysis for publication bias. When there is clear evidence of bias, it is unscientific to report the biased estimate. This would be like saying that the maximum optimistic estimate of global warming is that global warming does not exist. This is probably a true statement about the most optimistic estimate, but not a scientific estimate of the actual global warming that has been taking place. There is no place for optimism in science. Optimism is a bias and the aim of science is to remove bias. If DGPs wants to represent scientific psychology, the board should post what they consider the most accurate estimate of replicability in the OSF-project.

2. The widely cited 36% estimate is negative.

The board members then justify the publication of the maximally optimistic estimate as a strategy to counteract negative perceptions of psychology as a science in response to the finding that only 36% of results were replicated. The board members felt that these negative responses misrepresent the OSF-project and psychology as a scientific discipline.

„Dies wird weder dem Projekt der Open Science Collaboration noch unserer Disziplin insgesamt gerecht. Wir sollten jedoch bei der konstruktiven Bewältigung der Krise Vorreiter innerhalb der betroffenen Wissenschaften sein.“

However, reporting the dismal 36% replication rate of the OSF-replication project is not a criticism of the OSF-project. Rather, it assumes that the OSF-replication project was a rigorous and successful attempt to provide an estimate of the typical replicability of results published in top psychology journals. The outcome could have been 70% or 35%. The quality of the project does not depend on the result. The result is also not a negatively biased perception of psychology as a science. It is an objective scientific estimate of the probability that a reported significant result in a journal would produce a significant result again in a replication study.   Whether 36% is acceptable or not can be debated, but it seems problematic to post a maximally optimistic estimate to counteract negative implications of an objective estimate.

3. Is 36% replicability good or bad?

Next, the board ponders the implications of the 36% success rate. “How should we evaluate this number?” The board members do not know.  According to their official conclusion, this question is complex as divergent contributions on the discussion page suggest.

„Im Science-Artikel wurde die relative Häufigkeit der in den Replikationsstudien statistisch bedeutsamen Effekte mit 36% angegeben. Wie ist diese Zahl zu bewerten? Wie komplex die Antwort auf diese Frage ist, machen die Forumsbeiträge von Roland Deutsch, Klaus Fiedler, Moritz Heene (s.a. Heene & Schimmack) und Frank Renkewitz deutlich.“

To help the board members to understand the number, I can give a brief explanation of replicability. Although there are several ways to define replicability, one plausible definition of replicability is to equate it with statistical power. Statistical power is the probability that a study will produce a significant result. A study with 80% power has an 80% probability to produce a significant result. For a set of 100 studies, one would expect roughly 80 significant results and 20 non-significant results. For 100 studies with 36% power, one would expect roughly 36 significant results and 64 non-significant results. If researchers would publish all studies, the percentage of published significant results would provide an unbiased estimate of the typical power of studies.   However, it is well known that significant results are more likely to be written up, submitted for publication, and accepted for publication. These reporting biases explain why psychology journals report over 90% significant results, although the actual power of studies is less than 90%.

In 1962, Jacob Cohen provided the first attempt to estimate replicability of psychological results. His analysis suggested that psychological studies have approximately 50% power. He suggested that psychologists should increase power to 80% to provide robust evidence for effects and to avoid wasting resources on studies that cannot detect small, but practically important effects. For the next 50 years, psychologists have ignored Cohen’s warning that most studies are underpowered, despite repeated reminders that there are no signs of improvement, including reminders by prominent German psychologists like Gerg Giegerenzer, director of a Max Planck Institute (Sedlmeier & Giegerenzer, 1989; Maxwell, 2004; Schimmack, 2012).

The 36% success rate for an unbiased set of 100 replication studies, suggest that the actual power of published studies in psychology journals is 36%.  The power of all studies conducted is even lower because the p < .05 selection criterion favors studies with higher power.  Does the board think 36% power is an acceptable amount of power?

4. Psychologists should improve replicability in the future

On a positive note, the board members suggest that, after careful deliberation, psychologists need to improve replicability so that it can be demonstrated in a few years that replicability has increased.

„Wir müssen nach sorgfältiger Diskussion unter unseren Mitgliedern Maßnahmen ergreifen (bei Zeitschriften, in den Instituten, bei Förderorganisationen, etc.), die die Replikationsquote im temporalen Vergleich erhöhen können.“

The board members do not mention a simple solution to the replicabilty problem that was advocated over 50 years ago by Jacob Cohen. To increase replicability, psychologists have to think about the strength of the effects that they are investigating and they have to conduct studies that have a realistic chance to distinguish these effects from variation due to random error.   This often means investing more resources (larger samples, repeated trials, etc.) in a single study.   Unfortunately, the leaders of German psychologists appear to be unaware of this important and simple solution to the replication crisis. They neither mention power as a cause of the problem, nor do they recommend increasing power to increase replicability in the future.

5. Do the Results Reveal Fraud?

The DGPs board members then discuss the possibility that the OSF-reproducibilty results reveal fraud, like the fraud committed by Stapel. The board points out that the OSF-results do not imply that psychologists commit fraud because failed replications can occur for various reasons.

„Viele Medien (und auch einige Kolleginnen und Kollegen aus unserem Fach) nennen die Befunde der Science-Studie im gleichen Atemzug mit den Betrugsskandalen, die unser Fach in den letzten Jahren erschüttert haben. Diese Assoziation ist unserer Meinung nach problematisch: sie suggeriert, die geringe Replikationsrate sei auf methodisch fragwürdiges Verhalten der Autor(inn)en der Originalstudien zurückzuführen.“

It is true that the OSF-results do not reveal fraud. However, the board members confuse fraud with questionable research practices. Fraud is defined as fabricating data that were never collected. Only one of the 100 studies in the OSF-replication project (by Jens Förster, a former student of Fritz Strack, one of the board members) is currently being investigated for fraud by the University of Amsterdam.  Despite very strong results in the original study, it failed to replicate.

The more relevant question is how much questionable research practices contributed to the results. Questionable research practices are practices where data are being collected, but statistical results are only being reported if they produce a significant result (studies, conditions, dependent variables, data points that do not produce significant results are excluded from the results that are being submitted for publication. It has been known for over 50 years that these practices produce a discrepancy between the actual power of studies and the rate of significant results that are published in psychology journals (Sterling, 1959).

Recent statistical developments have made it possible to estimate the true power of studies after correcting for publication bias.   Based on these calculations, the true power of the original studies in the OSF-project was only 50%.   Thus a large portion of the discrepancy between nearly 100% reported significant results and a replication success rate of 36% is explained by publication bias (see R-Index blogs for social psychology and cognitive psychology).

Other factors may contribute to the discrepancy between the statistical prediction that the replication success rate would be 50% and the actual success rate of 36%. Nevertheless, the lion share of the discrepancy can be explained by the questionable practice to report only evidence that supports a hypothesis that a researcher wants to support. This motivated bias undermines the very foundations of science. Unfortunately, the board ignores this implication of the OSF results.

6. What can we do?

The board members have no answer to this important question. In the past four years, numerous articles have been published that have made suggestions how psychology can improve its credibility as a science. Yet, the DPfP board seems to be unaware of these suggestions or unable to comment on these proposals.

„Damit wären wir bei der Frage, die uns als Fachgesellschaft am stärksten beschäftigt und weiter beschäftigen wird. Zum einen brauchen wir eine sorgfältige Selbstreflexion über die Bedeutung von Replikationen in unserem Fach, über die Bedeutung der neuesten Science-Studie sowie der weiteren, zurzeit noch im Druck oder in der Phase der Auswertung befindlichen Projekte des Center for Open Science (wie etwa die Many Labs-Studien) und über die Grenzen unserer Methoden und Paradigmen“

The time for more discussion has passed. After 50 years of ignoring Jacob Cohen’s recommendation to increase statistical power it is time for action. If psychologists are serious about replicability, they have to increase the power of their studies.

The board then discusses the possibility of measuring and publishing replication rates at the level of departments or individual scientists. They are not in favor of such initiatives, but they provide no argument for their position.

„Datenbanken über erfolgreiche und gescheiterte Replikationen lassen sich natürlich auch auf der Ebene von Instituten oder sogar Personen auswerten (wer hat die höchste Replikationsrate, wer die niedrigste?). Sinnvoller als solche Auswertungen sind Initiativen, wie sie zurzeit (unter anderem) an der LMU an der LMU München implementiert wurden (siehe den Beitrag von Schönbrodt und Kollegen).“

The question is why replicability should not be measured and used to evaluate researchers. If the board really valued replicability and wanted to increase replicability in a few years, wouldn’t it be helpful to have a measure of replicability and to reward departments or researchers who invest more resources in high powered studies that can produce significant results without the need to hide disconfirming evidence in file-drawers?   A measure of replicability is also needed because current quantitative measures of scientific success are one of the reasons for the replicability crisis. The most successful researchers are those who publish the most significant results, no matter how these results were obtained (with the exception of fraud). To change this unscientific practice of significance chasing, it is necessary to have an alternative indicator of scientific quality that reflects how significant results were obtained.

Conclusion

The board makes some vague concluding remarks that are not worthwhile repeating here. So let me conclude with my own remarks.

The response of the DGPs board is superficial and does not engage with the actual arguments that were exchanged on the discussion page. Moreover, it ignores some solid scientific insights into the causes of the replicability crisis and it makes no concrete suggestions how German psychologists should change their behaviors to improve the credibility of psychology as a science. Not once do they point out that the results of the OSF-project were predictable based on the well-known fact that psychological studies are underpowered and that failed studies are hidden in file-drawers.

I received my education in Germany all the way to the Ph.D at the Free University in Berlin. I had several important professors and mentors that educated me about philosophy of science and research methods (Rainer Reisenzein, Hubert Feger, Hans Westmeyer, Wolfgang Schönpflug). I was a member of DGPs for many years. I do not believe that the opinion of the board members represent a general consensus among German psychologists. I hope that many German psychologists recognize the importance of replicability and are motivated to make changes to the way psychologists conduct research.  As I am no longer a member of DGfP, I have no direct influence on it, but I hope that the next election will elect a candidate that will promote open science, transparency, and above all scientific integrity.

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Replicability-Report for SOCIAL COGNITION

SOCIAL COGNITION is published by Guilford Press.

SCImago rankings of all psychology journals ranked SOCIAL COGNITION #178 with an SJR-Impact-Factor of 1.2 in 2014.

At present, the replicability-report is based on articles published from 1995 to 2015.  During this time, SOCIAL COGNITION published 550 articles.  The Replicability-Report is based on 450 articles that reported one or more t or F-test in the text (results reported in Figures or Tables are not included).  The test-statistic was converted into z-scores to estimate post-hoc-power.  The analysis is based on 5,331 z-scores in the range from 2 (just above the 1.96 criterion value for p < .05 (two-tailed) to 4.

PHP-Curve SocialCognition

Based on the distribution of z-scores in the range between 2 and 4, the average power for significant results in this range is estimated to be 55% with a homogeneous model, which is currently being used for the replicability ranking.  The average power assuming heterogeneity is 46%.  This estimate suggests that only half of the published results with z-scores in this range yield significant results in an exact replication study with the same sample size and power (results with z > 4 are expected to replicate with nearly 100%).

The same method was used to estimate power for individual years.

PHP-Trend SocialCognition

The results show a decreasing trend and the estimate for the current year is only 35%. This estimate could still increase as more articles from 2015 are being published.  However, the replicability score for SOCIAL COGNITION is low and raises concerns about the replicability of results published in this journal.   The same method produced a replicability score of 32% for social psychology results in the OSF-Reproducibilty Project. The actual rate of successful replications, including z-scores greater than 4, was 8% when sample size was held constant.   Thus, the replicability score of 35% for articles published in 2015 in SOCIAL COGNITION suggests that few of the theoretically important results published in SOCIAL COGNITION would replicate in an actual replication study.

The Replicability of Cognitive Psychology in the OSF-Reproducibility-Project

The OSF-Reproducibility Project (Psychology) aimed to replicate 100 results published in original research articles in three psychology journals in 2008. The selected journals focus on publishing results from experimental psychology. The main paradigm of experimental psychology is to recruit samples of participants and to study their behaviors in controlled laboratory conditions. The results are then generalized to the typical behavior of the average person.

An important methodological distinction in experimental psychology is the research design. In a within-subject design, participants are exposed to several (a minimum of two) situations and the question of interest is whether responses to one situation differ from behavior in other situations. The advantage of this design is that individuals serve as their own controls and variation due to unobserved causes (mood, personality, etc.) does not influence the results. This design can produce high statistical power to study even small effects. The design is often used by cognitive psychologists because the actual behaviors are often simple behaviors (e.g., pressing a button) that can be repeated many times (e.g., to demonstrate interference in the Stroop paradigm).

In a between-subject design, participants are randomly assigned to different conditions. A mean difference between conditions reveals that the experimental manipulation influenced behavior. The advantage of this design is that behavior is not influenced by previous behaviors in the experiment (carry over effects). The disadvantage is that many uncontrolled factors (e..g, mood, personality) also influence behavior. As a result, it can be difficult to detect small effects of an experimental manipulation among all of the other variance that is caused by uncontrolled factors. As a result, between-subject designs require large samples to study small effects or they can only be used to study large effects.

One of the main findings of the OSF-Reproducibility Project was that results from within-subject designs used by cognitive psychology were more likely to replicate than results from between-subject designs used by social psychologists. There were two few between-subject studies by cognitive psychologists or within-subject designs by social psychologists to separate these factors.   This result of the OSF-reproducibility project was predicted by PHP-curves of the actual articles as well as PHP-curves of cognitive and social journals (Replicability-Rankings).

Given the reliable difference between disciplines within psychology, it seems problematic to generalize the results of the OSF-reproducibility project across all areas of psychology. For this reason, I conducted separate analyses for social psychology and for cognitive psychology. This post examines the replicability of results in cognitive psychology. The results for social psychology are posted here.

The master data file of the OSF-reproducibilty project contained 167 studies with replication results for 99 studies. 42 replications were classified as cognitive studies. I excluded Reynolds and Bresner was excluded because the original finding was not significant. I excluded C Janiszewski, D Uy (doi:10.1111/j.1467-9280.2008.02057.x) because it examined the anchor effect, which I consider to be social psychology. Finally, I excluded two studies with children as participants because this research falls into developmental psychology (E Nurmsoo, P Bloom; V Lobue, JS DeLoache).

I first conducted a post-hoc-power analysis of the reported original results. Test statistics were first converted into two-tailed p-values and two-tailed p-values were converted into absolute z-scores using the formula (1 – norm.inverse(1-p/2). Post-hoc power was estimated by fitting the observed z-scores to predicted z-scores with a mixed-power model with three parameters (Brunner & Schimmack, in preparation).

Estimated power was 75%. This finding reveals the typical presence of publication bias because the actual success rate of 100% is too high given the power of the studies.  Based on this estimate, one would expect that only 75% of the 38 findings (k = 29) would produce a significant result in a set of 38 exact replication studies with the same design and sample size.

PHP-Curve OSF-REP Cognitive Original Data

The Figure visualizes the discrepancy between observed z-scores and the success rate in the original studies. Evidently, the distribution is truncated and suggests a file-drawer of missing studies with non-significant results. However, the mode of the curve (it’s highest point) is projected to be on the right side of the significance criterion (z = 1.96, p = .05 (two-tailed)), which suggests that more than 50% of results should replicate. Given the absence of reliable data in the range from 0 to 1.96, the data make it impossible to estimate the exact distribution in this region, but the gentle decline of z-scores on the right side of the significance criterion suggests that the file-drawer is relatively small.

Sample sizes of the replication studies were based on power analysis with the reported effect sizes. The problem with this approach is that the reported effect sizes are inflated and provide an inflated estimate of true power. With a true power estimate of 75%, the inflated power estimates were above 80% and often over 90%. As a result, many replication studies used the same sample size and some even used a smaller sample size because the original study appeared to be overpowered (the sample size was much larger than needed). The median sample size for the original studies was 32. The median sample size for the replication studies was N = 32. Changes in sample sizes make it difficult to compare the replication rate of the original studies with those of the replication study. Therefore, I adjusted the z-scores of the replication study to match z-scores that would have been obtained with the original sample size. Based on the post-hoc-power analysis above, I predicted that 75% of the replication studies would produce a significant result (k = 29). I also had posted predictions for individual studies based on a more comprehensive assessment of each article. The success rate for my a priori predictions was 69% (k = 27).

The actual replication rate based on adjusted z-scores was 63% (k = 22), although 3 studies produced only p-values between .05 and .06 after the adjustment was applied. If these studies were not counted, the success rate would have been 50% (19/38). This finding suggests that post-hoc power analysis overestimates true power by 10% to 25%. However, it is also possible that some of the replication studies failed to reproduce the exact experimental conditions of the original studies, which would lower the probability of obtaining a significant result. Moreover, the number of studies is very small and the discrepancy may simply be due to random sampling error. The important result is that post-hoc power curves correctly predict that the success rate in a replication study will be lower than the actual success rate because it corrects for the effect of publication bias. It also correctly predicts that a substantial number of studies will be successfully replicated, which they were. In comparison, post-hoc power analysis of social psychology predicted only 35% of successful replications and only 8% successfully replicated. Thus, post-hoc power analysis correctly predicts that results in cognitive psychology are more replicable than results in social psychology.

The next figure shows the post-hoc-power curve for the sample-size corrected z-scores of the replication studies.

PHP-Curve OSF-REP Cognitive Adj. Rep. Data

The PHP-Curve estimate of power for z-scores in the range from 0 to 4 is 53% for the heterogeneous model that fits the data better than a homogeneous model. The shape of the distribution suggests that several of the non-significant results are type-II errors; that is, the studies had insufficient statistical power to demonstrate a real effect.

I also conducted a power analysis that was limited to the non-significant results. The estimated average power was 22%. This power is a mixture of true power in different studies and may contain some cases of true false positives (power = .05), but the existing data are insufficient to determine whether results are true false positives or whether a small effect is present and sample sizes were too small to detect it. Again, it is noteworthy that the same analysis for social psychology produced an estimate of 5%, which suggests that most of the non-significant results in social psychology are true false positives (the null-effect is true).

Below I discuss my predictions of individual studies.

Eight studies reported an effect with a z-score greater than 4 (4 sigma), and I predicted that all of the 4-sigma effects would replicate. 7 out of 8 effects were successfully replicated (D Ganor-Stern, J Tzelgov; JI Campbell, ND Robert; M Bassok, SF Pedigo, AT Oskarsson; PA White; E Vul, H Pashler; E Vul, M Nieuwenstein, N Kanwisher; J Winawer, AC Huk, L Boroditsky). The only exception was CP Beaman, I Neath, AM Surprenant (DOI: 10.1037/0278-7393.34.1.219). It is noteworthy that the sample size of the original study was N = 99 and the sample size of the replication study was N = 14. Even with an adjusted z-score the study produced a non-significant result (p = .19). However, small samples produce less reliable results and it would be interesting to examine whether the result would become significant with an actual sample of 99 participants.

Based on more detailed analysis of individual articles, I predicted that an additional 19 studies would replicate. However, 9 out these 19 studies were not successfully replicated. Thus, my predictions of additional successful replications are just at chance level, given the overall success rate of 50%.

Based on more detailed analysis of individual articles, I predicted that 11 studies would not replicate. However, 5 out these 11 studies were successfully replicated. Thus, my predictions of failed replications are just at chance level, given the overall success rate of 50%.

In short, my only rule that successfully predicted replicability of individual studies was the 4-sigma rule that predicts that all findings with a z-score greater than 4 will replicate.

In conclusion, a replicability of 50-60% is consistent with Cohen’s (1962) suggestion that typical studies in psychology have 60% power. Post-hoc power analysis slightly overestimated the replicability of published findings despite its ability to correct for publication bias. Future research needs to examine the sources that lead to a discrepancy between predicted and realized success rate. It is possible that some of this discrepancy is due to moderating factors. Although a replicability of 50-60% is not as catastrophic as the results for social psychology with estimates in the range from 8-35%, cognitive psychologists should aim to increase the replicability of published results. Given the widespread use of powerful within-subject designs, this is easily achieved by a modest increase in sample sizes from currently 30 participants to 50 participants, which would increase power from 60% to 80%.

Replicability-Report for SOCIAL PSYCHOLOGY AND PERSONALITY SCIENCE

SOCIAL PSYCHOLOGY AND PERSONALITY SCIENCE (SPPS) is sponsored by several psychological organizations: Association for Research in Personality (ARP), the European Association of Social Psychology (EASP), the Society of Experimental Social Psychology (SESP), the Society for Personality and Social Psychology (SPSP). The journal started publishing articles in 2010.

SCImago ranks SPPS as #57 of all psychology journals with an SJR-Impact-Factor of 2.1 in 2014.At present, the replicability-report is based on articles published from inception in 2010 to 2015. During this time, SPPS published 520 articles. The replicability-report is based on 378 articles that reported one or more t or F-test in the text of the results section (results reported in Figures or Tables are not included).  The test-statistic was converted into z-scores to estimate post-hoc-power.  The analysis is based on 1,879 z-scores in the range from 2, just above the 1.96 criterion value for p < .05 (two-tailed), to 4.

PHP-Curve SPPS

Based on the distribution of z-scores in the range between 2 and 4, the average power for significant results in this range is estimated to be 52%. This estimate suggests that only half of the published significant results in this range are predicted to produce a significant results in an exact replication study with the same sample size and power (results with z > 4 are expected to replicate with nearly 100%).

The same method was used to estimate power for individual years.

PHP-Trend SPPS

The results show a notable increase in the current year.  This increase may represent a change in the selection criteria in response to the replicability crisis in psychology. However, the 2015 score can still change as more data are becoming available.

Replicability-Report for EMOTION

EMOTION is a journal of the American Psychological Association.  It started publishing articles in 2001.

SCImago ranks EMOTION as #60 of all psychology journals with an SJR-Impact-Factor of 2.00 in 2014.

At present, the replicability-report is based on articles published from inception in 2001 to 2015. During this time, EMOTION published 1182 articles. The replicability-report is based on 1034 articles that reported one or more t or F-test in the text of the results section (results reported in Figures or Tables are not included).  The test-statistic was converted into z-scores to estimate post-hoc-power.  The analysis is based on 6,932 z-scores in the range from 2, just above the 1.96 criterion value for p < .05 (two-tailed), to 4.

PHP-Curve Emotion

Based on the distribution of z-scores in the range between 2 and 4, the average power for significant results in this range is estimated to be 61%. This estimate suggests that only 61% of the published significant results in this range are predicted to produce a significant results in an exact replication study with the same sample size and power (results with z > 4 are expected to replicate with nearly 100%).

The same method was used to estimate power for individual years.

PHP-Trend EMOTION

The results show a decrease in power over time.  In the past 4 years, all power estimates are below the historic average. In the current year, the replicability score is 52.   There is no indication that power of published studies is increasing in response to the replicability crisis in psychology.

REPLICABILITY RANKING OF 26 PSYCHOLOGY JOURNALS

THEORETICAL BACKGROUND

Neyman & Pearson (1933) developed the theory of type-I and type-II errors in statistical hypothesis testing.

A type-I error is defined as the probability of rejecting the null-hypothesis (i.e., the effect size is zero) when the null-hypothesis is true.

A type-II error is defined as the probability of failing to reject the null-hypothesis when the null-hypothesis is false (i.e., there is an effect).

A common application of statistics is to provide empirical evidence for a theoretically predicted relationship between two variables (cause-effect or covariation). The results of an empirical study can produce two outcomes. Either the result is statistically significant or it is not statistically significant. Statistically significant results are interpreted as support for a theoretically predicted effect.

Statistically non-significant results are difficult to interpret because the prediction may be false (the null-hypothesis is true) or a type-II error occurred (the theoretical prediction is correct, but the results fail to provide sufficient evidence for it).

To avoid type-II errors, researchers can design studies that reduce the type-II error probability. The probability of avoiding a type-II error when a predicted effect exists is called power. It could also be called the probability of success because a significant result can be used to provide empirical support for a hypothesis.

Ideally researchers would want to maximize power to avoid type-II errors. However, powerful studies require more resources. Thus, researchers face a trade-off between the allocation of resources and their probability to obtain a statistically significant result.

Jacob Cohen dedicated a large portion of his career to help researchers with the task of planning studies that can produce a successful result, if the theoretical prediction is true. He suggested that researchers should plan studies to have 80% power. With 80% power, the type-II error rate is still 20%, which means that 1 out of 5 studies in which a theoretical prediction is true would fail to produce a statistically significant result.

Cohen (1962) examined the typical effect sizes in psychology and found that the typical effect size for the mean difference between two groups (e.g., men and women or experimental vs. control group) is about half-of a standard deviation. The standardized effect size measure is called Cohen’s d in his honor. Based on his review of the literature, Cohen suggested that an effect size of d = .2 is small, d = .5 moderate, and d = .8. Importantly, a statistically small effect size can have huge practical importance. Thus, these labels should not be used to make claims about the practical importance of effects. The main purpose of these labels is that researchers can better plan their studies. If researchers expect a large effect (d = .8), they need a relatively small sample to have high power. If researchers expect a small effect (d = .2), they need a large sample to have high power.   Cohen (1992) provided information about effect sizes and sample sizes for different statistical tests (chi-square, correlation, ANOVA, etc.).

Cohen (1962) conducted a meta-analysis of studies published in a prominent psychology journal. Based on the typical effect size and sample size in these studies, Cohen estimated that the average power in studies is about 60%. Importantly, this also means that the typical power to detect small effects is less than 60%. Thus, many studies in psychology have low power and a high type-II error probability. As a result, one would expect that journals often report that studies failed to support theoretical predictions. However, the success rate in psychological journals is over 90% (Sterling, 1959; Sterling, Rosenbaum, & Weinkam, 1995). There are two explanations for discrepancies between the reported success rate and the success probability (power) in psychology. One explanation is that researchers conduct multiple studies and only report successful studies. The other studies remain unreported in a proverbial file-drawer (Rosenthal, 1979). The other explanation is that researchers use questionable research practices to produce significant results in a study (John, Loewenstein, & Prelec, 2012). Both practices have undesirable consequences for the credibility and replicability of published results in psychological journals.

A simple solution to the problem would be to increase the statistical power of studies. If the power of psychological studies in psychology were over 90%, a success rate of 90% would be justified by the actual probability of obtaining significant results. However, meta-analysis and method articles have repeatedly pointed out that psychologists do not consider statistical power in the planning of their studies and that studies continue to be underpowered (Maxwell, 2004; Schimmack, 2012; Sedlmeier & Giegerenzer, 1989).

One reason for the persistent neglect of power could be that researchers have no awareness of the typical power of their studies. This could happen because observed power in a single study is an imperfect indicator of true power (Yuan & Maxwell, 2005). If a study produced a significant result, the observed power is at least 50%, even if the true power is only 30%. Even if the null-hypothesis is true, and researchers publish only type-I errors, observed power is dramatically inflated to 62%, when the true power is only 5% (the type-I error rate). Thus, Cohen’s estimate of 60% power is not very reassuring.

Over the past years, Schimmack and Brunner have developed a method to estimate power for sets of studies with heterogeneous designs, sample sizes, and effect sizes. A technical report is in preparation. The basic logic of this approach is to convert results of all statistical tests into z-scores using the one-tailed p-value of a statistical test.  The z-scores provide a common metric for observed statistical results. The standard normal distribution predicts the distribution of observed z-scores for a fixed value of true power.   However, for heterogeneous sets of studies the distribution of z-scores is a mixture of standard normal distributions with different weights attached to various power values. To illustrate this method, the histograms of z-scores below show simulated data with 10,000 observations with varying levels of true power: 20% null-hypotheses being true (5% power), 20% of studies with 33% power, 20% of studies with 50% power, 20% of studies with 66% power, and 20% of studies with 80% power.

RepRankSimulation

The plot shows the distribution of absolute z-scores (there are no negative effect sizes). The plot is limited to z-scores below 6 (N = 99,985 out of 10,000). Z-scores above 6 standard deviations from zero are extremely unlikely to occur by chance. Even with a conservative estimate of effect size (lower bound of 95% confidence interval), observed power is well above 99%. Moreover, quantum physics uses Z = 5 as a criterion to claim success (e.g., discovery of Higgs-Boson Particle). Thus, Z-scores above 6 can be expected to be highly replicable effects.

Z-scores below 1.96 (the vertical dotted red line) are not significant for the standard criterion of (p < .05, two-tailed). These values are excluded from the calculation of power because these results are either not reported or not interpreted as evidence for an effect. It is still important to realize that true power of all experiments would be lower if these studies were included because many of the non-significant results are produced by studies with 33% power. These non-significant results create two problems. Researchers wasted resources on studies with inconclusive results and readers may be tempted to misinterpret these results as evidence that an effect does not exist (e.g., a drug does not have side effects) when an effect is actually present. In practice, it is difficult to estimate power for non-significant results because the size of the file-drawer is difficult to estimate.

It is possible to estimate power for any range of z-scores, but I prefer the range of z-scores from 2 (just significant) to 4. A z-score of 4 has a 95% confidence interval that ranges from 2 to 6. Thus, even if the observed effect size is inflated, there is still a high chance that a replication study would produce a significant result (Z > 2). Thus, all z-scores greater than 4 can be treated as cases with 100% power. The plot also shows that conclusions are unlikely to change by using a wider range of z-scores because most of the significant results correspond to z-scores between 2 and 4 (89%).

The typical power of studies is estimated based on the distribution of z-scores between 2 and 4. A steep decrease from left to right suggests low power. A steep increase suggests high power. If the peak (mode) of the distribution were centered over Z = 2.8, the data would conform to Cohen’s recommendation to have 80% power.

Using the known distribution of power to estimate power in the critical range gives a power estimate of 61%. A simpler model that assumes a fixed power value for all studies produces a slightly inflated estimate of 63%. Although the heterogeneous model is correct, the plot shows that the homogeneous model provides a reasonable approximation when estimates are limited to a narrow range of Z-scores. Thus, I used the homogeneous model to estimate the typical power of significant results reported in psychological journals.

DATA

The results presented below are based on an ongoing project that examines power in psychological journals (see results section for the list of journals included so far). The set of journals does not include journals that primarily publish reviews and meta-analysis or clinical and applied journals. The data analysis is limited to the years from 2009 to 2015 to provide information about the typical power in contemporary research. Results regarding historic trends will be reported in a forthcoming article.

I downloaded pdf files of all articles published in the selected journals and converted the pdf files to text files. I then extracted all t-tests and F-tests that were reported in the text of the results section searching for t(df) or F(df1,df2). All t and F statistics were converted into one-tailed p-values and then converted into z-scores.

RepRankAll

The plot above shows the results based on 218,698 t and F tests reported between 2009 and 2015 in the selected psychology journals. Unlike the simulated data, the plot shows a steep drop for z-scores just below the threshold of significance (z = 1.96). This drop is due to the tendency not to publish or report non-significant results. The heterogeneous model uses the distribution of non-significant results to estimate the size of the file-drawer (unpublished non-significant results). However, for the present purpose the size of the file-drawer is irrelevant because power is estimated only for significant results for Z-scores between 2 and 4.

The green line shows the best fitting estimate for the homogeneous model. The red curve shows fit of the heterogeneous model. The heterogeneous model is doing a much better job at fitting the long tail of highly significant results, but for the critical interval of z-scores between 2 and 4, the two models provide similar estimates of power (55% homogeneous & 53% heterogeneous model).   If the range is extended to z-scores between 2 and 6, power estimates diverge (82% homogenous, 61% heterogeneous). The plot indicates that the heterogeneous model fits the data better and that the 61% estimate is a better estimate of true power for significant results in this range. Thus, the results are in line with Cohen (1962) estimate that psychological studies average 60% power.

REPLICABILITY RANKING

The distribution of z-scores between 2 and 4 was used to estimate the average power separately for each journal. As power is the probability to obtain a significant result, this measure estimates the replicability of results published in a particular journal if researchers would reproduce the studies under identical conditions with the same sample size (exact replication). Thus, even though the selection criterion ensured that all tests produced a significant result (100% success rate), the replication rate is expected to be only about 50%, even if the replication studies successfully reproduce the conditions of the published studies. The table below shows the replicability ranking of the journals, the replicability score, and a grade. Journals are graded based on a scheme that is similar to grading schemes for undergraduate students (below 50 = F, 50-59 = E, 60-69 = D, 70-79 = C, 80-89 = B, 90+ = A).

ReplicabilityRanking

The average value in 2000-2014 is 57 (D+). The average value in 2015 is 58 (D+). The correlation for the values in 2010-2014 and those in 2015 is r = .66.   These findings show that the replicability scores are reliable and that journals differ systematically in the power of published studies.

LIMITATIONS

The main limitation of the method is that focuses on t and F-tests. The results might change when other statistics are included in the analysis. The next goal is to incorporate correlations and regression coefficients.

The second limitation is that the analysis does not discriminate between primary hypothesis tests and secondary analyses. For example, an article may find a significant main effect for gender, but the critical test is whether gender interacts with an experimental manipulation. It is possible that some journals have lower scores because they report more secondary analyses with lower power. To address this issue, it will be necessary to code articles in terms of the importance of statistical test.

The ranking for 2015 is based on the currently available data and may change when more data become available. Readers should also avoid interpreting small differences in replicability scores as these scores are likely to fluctuate. However, the strong correlation over time suggests that there are meaningful differences in the replicability and credibility of published results across journals.

CONCLUSION

This article provides objective information about the replicability of published findings in psychology journals. None of the journals reaches Cohen’s recommended level of 80% replicability. Average replicability is just about 50%. This finding is largely consistent with Cohen’s analysis of power over 50 years ago. The publication of the first replicability analysis by journal should provide an incentive to editors to increase the reputation of their journal by paying more attention to the quality of the published data. In this regard, it is noteworthy that replicability scores diverge from traditional indicators of journal prestige such as impact factors. Ideally, the impact of an empirical article should be aligned with the replicability of the empirical results. Thus, the replicability index may also help researchers to base their own research on credible results that are published in journals with a high replicability score and to avoid incredible results that are published in journals with a low replicability score. Ultimately, I can only hope that journals will start competing with each other for a top spot in the replicability rankings and as a by-product increase the replicability of published findings and the credibility of psychological science.

When Exact Replications Are Too Exact: The Lucky-Bounce-Test for Pairs of Exact Replication Studies

Imagine an NBA player has an 80% chance to make one free throw. What is the chance that he makes both free throws? The correct answer is 64% (80% * 80%).

Now consider the possibility that it is possible to distinguish between two types of free throws. Some free throws are good; they don’t touch the rim and make a swishing sound when they go through the net (all net). The other free throws bounce of the rim and go in (rattling in).

What is the probability that an NBA player with an 80% free throw percentage makes a free throw that is all net or rattles in? It is more likely that an NBA player with an 80% free throw average makes a perfect free throw because a free throw that rattles in could easily have bounded the wrong way, which would lower the free throw percentage. To achieve an 80% free throw percentage, most free throws have to be close to perfect.

Let’s say the probability of hitting the rim and going in is 30%. With an 80% free throw average, this means that the majority of free throws are in the close-to-perfect category (20% misses, 30% rattle-in, 50% close-to-perfect).

What does this have to do with science? A lot!

The reason is that the outcome of a scientific study is a bit like throwing free throws. One factor that contributes to a successful study is skill (making correct predictions, avoiding experimenter errors, and conducting studies with high statistical power). However, another factor is random (a lucky or unlucky bounce).

The concept of statistical power is similar to an NBA players’ free throw percentage. A researcher who conducts studies with 80% statistical power is going to have an 80% success rate (that is, if all predictions are correct). In the remaining 20% of studies, a study will not produce a statistically significant result, which is equivalent to missing a free throw and not getting a point.

Many years ago, Jacob Cohen observed that researchers often conduct studies with relatively low power to produce a statistically significant result. Let’s just assume right now that a researcher conducts studies with 60% power. This means, researchers would be like NBA players with a 60% free-throw average.

Now imagine that researchers have to demonstrate an effect not only once, but also a second time in an exact replication study. That is researchers have to make two free throws in a row. With 60% power, the probability to get two significant results in a row is only 36% (60% * 60%). Moreover, many of the freethrows that are made rattle in rather than being all net. The percentages are about 40% misses, 30% rattling in and 30% all net.

One major difference between NBA players and scientists is that NBA players have to demonstrate their abilities in front of large crowds and TV cameras, whereas scientists conduct their studies in private.

Imagine an NBA player could just go into a private room, throw two free throws and then report back how many free throws he made and the outcome of these free throws determine who wins game 7 in the playoff finals. Would you trust the player to tell the truth?

If you would not trust the NBA player, why would you trust scientists to report failed studies? You should not.

It can be demonstrated statistically that scientists are reporting more successes than the power of their studies would justify (Sterling et al., 1995; Schimmack, 2012). Amongst scientists this fact is well known, but the general public may not fully appreciate the fact that a pair of exact replication studies with significant results is often just a selection of studies that included failed studies that were not reported.

Fortunately, it is possible to use statistics to examine whether the results of a pair of studies are likely to be honest or whether failed studies were excluded. The reason is that an amateur is not only more likely to miss a free throw. An amateur is also less likely to make a perfect free throw.

Based on the theory of statistical power developed by Nyman and Pearson and popularized by Jacob Cohen, it is possible to make predictions about the relative frequency of p-values in the non-significant (failure), just significant (rattling in), and highly significant (all net) ranges.

As for made-free-throws, the distinction between lucky and clear successes is somewhat arbitrary because power is continuous. A study with a p-value of .0499 is very lucky because p = .501 would have been not significant (rattled in after three bounces on the rim). A study with p = .000001 is a clear success. Lower p-values are better, but where to draw the line?

As it turns out, Jacob Cohen’s recommendation to conduct studies with 80% power provides a useful criterion to distinguish lucky outcomes and clear successes.

Imagine a scientist conducts studies with 80% power. The distribution of observed test-statistics (e.g. z-scores) shows that this researcher has a 20% chance to get a non-significant result, a 30% chance to get a lucky significant result (p-value between .050 and .005), and a 50% chance to get a clear significant result (p < .005). If the 20% failed studies are hidden, the percentage of results that rattled in versus studies with all-net results are 37 vs. 63%. However, if true power is just 20% (an amateur), 80% of studies fail, 15% rattle in, and 5% are clear successes. If the 80% failed studies are hidden, only 25% of the successful studies are all-net and 75% rattle in.

One problem with using this test to draw conclusions about the outcome of a pair of exact replication studies is that true power is unknown. To avoid this problem, it is possible to compute the maximum probability of a rattling-in result. As it turns out, the optimal true power to maximize the percentage of lucky outcomes is 66% power. With true power of 66%, one would expect 34% misses (p > .05), 32% lucky successes (.050 < p < .005), and 34% clear successes (p < .005).

LuckyBounceTest

For a pair of exact replication studies, this means that there is only a 10% chance (32% * 32%) to get two rattle-in successes in a row. In contrast, there is a 90% chance that misses were not reported or that an honest report of successful studies would have produced at least one all-net result (z > 2.8, p < .005).

Example: Unconscious Priming Influences Behavior

I used this test to examine a famous and controversial set of exact replication studies. In Bargh, Chen, and Burrows (1996), Dr. Bargh reported two exact replication studies (studies 2a and 2b) that showed an effect of a subtle priming manipulation on behavior. Undergraduate students were primed with words that are stereotypically associated with old age. The researchers then measured the walking speed of primed participants (n = 15) and participants in a control group (n = 15).

The two studies were not only exact replications of each other; they also produced very similar results. Most readers probably expected this outcome because similar studies should produce similar results, but this false belief ignores the influence of random factors that are not under the control of a researcher. We do not expect lotto winners to win the lottery again because it is an entirely random and unlikely event. Experiments are different because there could be a systematic effect that makes a replication more likely, but in studies with low power results should not replicate exactly because random sampling error influences results.

Study 1: t(28) = 2.86, p = .008 (two-tailed), z = 2.66, observed power = 76%
Study 2: t(28) = 2.16, p = .039 (two-tailed), z = 2.06, observed power = 54%

The median power of these two studies is 65%. However, even if median power were lower or higher, the maximum probability of obtaining two p-values in the range between .050 and .005 remains just 10%.

Although this study has been cited over 1,000 times, replication studies are rare.

One of the few published replication studies was reported by Cesario, Plaks, and Higgins (2006). Naïve readers might take the significant results in this replication study as evidence that the effect is real. However, this study produced yet another lucky success.

Study 3: t(62) = 2.41, p = .019, z = 2.35, observed power = 65%.

The chances of obtaining three lucky successes in a row is only 3% (32% *32% * 32*). Moreover, with a median power of 65% and a reported success rate of 100%, the success rate is inflated by 35%. This suggests that the true power of the reported studies is considerably lower than the observed power of 65% and that observed power is inflated because failed studies were not reported.

The R-Index corrects for inflation by subtracting the inflation rate from observed power (65% – 35%). This means the R-Index for this set of published studies is 30%.

This R-Index can be compared to several benchmarks.

An R-Index of 22% is consistent with the null-hypothesis being true and failed attempts are not reported.

An R-Index of 40% is consistent with 30% true power and all failed attempts are not reported.

It is therefore not surprising that other researchers were not able to replicate Bargh’s original results, even though they increased statistical power by using larger samples (Pashler et al. 2011, Doyen et al., 2011).

In conclusion, it is unlikely that Dr. Bargh’s original results were the only studies that they conducted. In an interview, Dr. Bargh revealed that the studies were conducted in 1990 and 1991 and that they conducted additional studies until the publication of the two studies in 1996. Dr. Bargh did not reveal how many studies they conducted over the span of 5 years and how many of these studies failed to produce significant evidence of priming. If Dr. Bargh himself conducted studies that failed, it would not be surprising that others also failed to replicate the published results. However, in a personal email, Dr. Bargh assured me that “we did not as skeptics might presume run many studies and only reported the significant ones. We ran it once, and then ran it again (exact replication) in order to make sure it was a real effect.” With a 10% probability, it is possible that Dr. Bargh was indeed lucky to get two rattling-in findings in a row. However, his aim to demonstrate the robustness of an effect by trying to show it again in a second small study is misguided. The reason is that it is highly likely that the effect will not replicate or that the first study was already a lucky finding after some failed pilot studies. Underpowered studies cannot provide strong evidence for the presence of an effect and conducting multiple underpowered studies reduces the credibility of successes because the probability of this outcome to occur even when an effect is present decreases with each study (Schimmack, 2012). Moreover, even if Bargh was lucky to get two rattling-in results in a row, others will not be so lucky and it is likely that many other researchers tried to replicate this sensational finding, but failed to do so. Thus, publishing lucky results hurts science nearly as much as the failure to report failed studies by the original author.

Dr. Bargh also failed to realize how lucky he was to obtain his results, in his response to a published failed-replication study by Doyen. Rather than acknowledging that failures of replication are to be expected, Dr. Bargh criticized the replication study on methodological grounds. There would be a simple solution to test Dr. Bargh’s hypothesis that he is a better researcher and that his results are replicable when the study is properly conducted. He should demonstrate that he can replicate the result himself.

In an interview, Tom Bartlett asked Dr. Bargh why he didn’t conduct another replication study to demonstrate that the effect is real. Dr. Bargh’s response was that “he is aware that some critics believe he’s been pulling tricks, that he has a “special touch” when it comes to priming, a comment that sounds like a compliment but isn’t. “I don’t think anyone would believe me,” he says.” The problem for Dr. Bargh is that there is no reason to believe his original results, either. Two rattling-in results alone do not constitute evidence for an effect, especially when this result could not be replicated in an independent study. NBA players have to make free-throws in front of a large audience for a free-throw to count. If Dr. Bargh wants his findings to count, he should demonstrate his famous effect in an open replication study. To avoid embarrassment, it would be necessary to increase the power of the replication study because it is highly unlikely that even Dr. Bargh can continuously produce significant results with samples of N = 30 participants. Even if the effect is real, sampling error is simply too large to demonstrate the effect consistently. Knowledge about statistical power is power. Knowledge about post-hoc power can be used to detect incredible results. Knowledge about a priori power can be used to produce credible results.

Swish!