Category Archives: Replicability

Once a p-hacker, always a p-hacker?

The 2010s have seen a replication crisis in social psychology (Schimmack, 2020). The main reason why it is difficult to replicate results from social psychology is that researchers used questionable research practices (QRPs, John et al., 2012) to produce more significant results than their low-powered designs warranted. A catchy term for these practices is p-hacking (Simonsohn, 2014).

New statistical techniques made it possible to examine whether published results were obtained with QRPs. In 2012, I used the incredibility index to show that Bem (2011) used QRPs to provide evidence for extrasensory perception (Schimmack, 2012). In the same article, I also suggested that Gailliot, Baumeister, DeWall, Maner, Plant, Tice, and Schmeichel, (2007) used QRPs to present evidence that suggested will-power relies on blood glucose levels. During the review process of my manuscript, Baumeister confirmed that QRPs were used (cf. Schimmack, 2014). Baumeister defended the use of these practices with a statement that the use of these practices was the norm in social psychology and that the use of these practices was not considered unethical.

The revelation that research practices were questionable casts a shadow on the history of social psychology. However, many also saw it as an opportunity to change and improve these practices (Świątkowski and Dompnier, 2017). Over the past decades, the evaluation of QRPs has changed. Many researchers now recognize that these practices inflate error rates, make published results difficult to replicate, and undermine the credibility of psychological science (Lindsay, 2019).

However, there are no general norms regarding these practices and some researchers continue to use them (e.g., Adam D. Galinsky, cf. Schimmack, 2019). This makes it difficult for readers of the social psychological literature to identify research that can be trusted or not, and the answer to this question has to be examined on a case by case basis. In this blog post, I examine the responses of Baumeister, Vohs, DeWall, and Schmeichel to the replication crisis and concerns that their results provide false evidence about the causes of will-power (Friese, Loschelder , Gieseler , Frankenbach & Inzlicht, 2019; Inzlicht, 2016).

To examine this question scientifically, I use test-statistics that are automatically extracted from psychology journals. I divide the test-statistics into those that were obtained until 2012, when awareness about QRPs emerged, and those published after 2012. The test-statistics are examined using z-curve (Brunner & Schimmack, 2019; Bartos & Schimmack, 2020). Results provide information about the expected replication rate and discovery rate. The use of QRPs is examined by comparing the observed discovery rate (how many published results are significant) to the expected discovery rate (how many tests that were conducted produced significant results).

Roy F. Baumeister’s replication rate was 60% (53% to 67%) before 2012 and 65% (57% to 74%) after 2012. The overlap of the 95% confidence intervals indicates that this small increase is not statistically reliable. Before 2012, the observed discovery rate was 70% and it dropped to 68% after 2012. Thus, there is no indication that non-significant results are reported more after 2012. The expected discovery rate was 32% before 2012 and 25% after 2012. Thus, there is also no change in the expected discovery rate and the expected discovery rate is much lower than the observed discovery rate. This discrepancy shows that QRPs were used before 2012 and after 2012. The 95%CI do not overlap before and after 2012, indicating that this discrepancy is statistically significant. Figure 1 shows the influence of QRPs when the observed non-significant results (histogram of z-scores below 1.96 in blue) is compared to the model prediction (grey curve). The discrepancy suggests a large file drawer of unreported statistical tests.

An old saying is that you can’t teach an old dog new tricks. So, the more interesting question is whether the younger contributors to the glucose paper changed their research practices.

The results for C. Nathan DeWall show no notable response to the replication crisis (Figure 2). The expected replication rate increased slightly from 61% to 65%, but the difference is not significant and visual inspection of the plots suggests that it is mostly due to a decrease in reporting p-values just below .05. One reason for this might be a new goal to p-hack at least to the level of .025 to avoid detection of p-hacking by p-curve analysis. The observed discovery rate is practically unchanged from 68% to 69%. The expected discovery rate increased only slightly from 28% to 35%, but the difference is not significant. More important, the expected discovery rates are significantly lower than the observed discovery rates before and after 2012. Thus, there is evidence that DeWall used questionable research practices before and after 2012, and there is no evidence that he changed his research practices.

The results for Brandon J. Schmeichel are even more discouraging (Figure 3). Here the expected replication rate decreased from 70% to 56%, although this decrease is not statistically significant. The observed discovery rate decreased significantly from 74% to 63%, which shows that more non-significant results are reported. Visual inspection shows that this is particularly the case for test-statistics close to zero. Further inspection of the article would be needed to see how these results are interpreted. More important, The expected discovery rates are significantly lower than the observed discovery rates before 2012 and after 2012. Thus, there is evidence that QRPs were used before and after 2012 to produce significant results. Overall, there is no evidence that research practices changed in response to the replication crisis.

The results for Kathleen D. Vohs also show no response to the replication crisis (Figure 4). The expected replication rate dropped slightly from 62% to 58%; the difference is not significant. The observed discovery rate dropped slightly from 69% to 66%, and the expected discovery rate decreased from 43% to 31%, although this difference is also not significant. Most important, the observed discovery rates are significantly higher than the expected discovery rates before 2012 and after 2012. Thus, there is clear evidence that questionable research practices were used before and after 2012 to inflate the discovery rate.

Conclusion

After concerns about research practices and replicability emerged in the 2010s, social psychologists have debated this issue. Some social psychologists changed their research practices to increase statistical power and replicability. However, other social psychologists have denied that there is a crisis and attributed replication failures to a number of other causes. Not surprisingly, some social psychologists also did not change their research practices. This blog post shows that Baumeister and his students have not changed research practices. They are able to publish questionable research because there has been no collective effort to define good research practices and to ban questionable practices and to treat the hiding of non-significant results as a breach of research ethics. Thus, Baumeister and his students are simply exerting their right to use questionable research practices, whereas others voluntarily implemented good, open science, practices. Given the freedom of social psychologists to decide which practices they use, social psychology as a field continuous to have a credibility problem. Editors who accept questionable research in their journals are undermining the credibility of their journal. Authors are well advised to publish in journals that emphasis replicability and credibility with open science badges and with a high replicability ranking (Schimmack, 2019).

Why Frontiers Should Retract Baumeister’s Critique of Carter’s Meta-Analysis

This blog post is heavily based on one of my first blog-posts in 2014 (Schimmack, 2014).  The blog post reports a meta-analysis of ego-depletion studies that used the hand-grip paradigm.  When I first heard about the hand-grip paradigm, I thought it was stupid because there is so much between-subject variance in physical strength.  However, then I learned that it is the only paradigm that uses a pre-post design, which removes between-subject variance from the error term. This made the hand-grip paradigm the most interesting paradigm because it has the highest power to detect ego-depletion effects.  I conducted a meta-analysis of the hand-grip studies and found clear evidence of publication bias.  This finding is very damaging to the wider ego-depletion research because other studies used between-subject designs with small samples which have very low power to detect small effects.

This prediction was confirmed in meta-analyses by Carter,E.C., Kofler, L.M., Forster, D.E., and McCulloch,M.E. (2015) that revealed publication bias in ego-depletion studies with other paradigms.

The results also explain why attempts to show ego-depletion effects with within-subject designs failed (Francis et al., 2018).  Within-subject designs increase power by removing fixed between-subject variance such as physical strength.  However, given the lack of evidence with the hand-grip paradigm it is not surprising that within-subject designs also failed to show ego-depletion effects with other dependent variables in within-subject designs.  Thus, these results further suggest that ego-depletion effects are too small to be used for experimental investigations of will-power.

Of course, Roy F. Baumeister doesn’t like this conclusion because his reputation is to a large extent based on the resource model of will-power.  His response to the evidence that most of the evidence is based on questionable practices that produced illusory evidence has been to attack the critics (cf. Schimmack, 2019).

In 2016, he paid to publish a critique of Carter’s (2015) meta-analysis in Frontiers of Psychology (Cunningham & Baumeister, 2016).   In this article, the authors question the results obtained by bias-tests that reveal publication bias and suggest that there is no evidence for ego-depletion effects.

Unfortunately, Cunningham and Baumeister’s (2016) article is cited frequently as if it contained some valid scientific arguments.

For example, Christodoulou, Lac, and Moore (2017) cite the article to dismiss the results of a PEESE analysis that suggests publication bias is present and there is no evidence that infants can add and subtract. Thus, there is a real danger that meta-analysts will use Cunningham & Baumeister’s (2016) article to dismiss evidence of publication bias and to provide false evidence for claims that rest on questionable research practices.

Fact Checking Cunningham and Baumeister’s Criticisms

Cunningham and Baumeister (2016) claim that results from bias tests are difficult to interpret, but there criticism is based on false arguments and inaccurate claims.

Confusing Samples and Populations

This scientifically sounding paragraph is a load of bull. The authors claim that inferential tests require sampling from a population and raise a question about the adequacy of a sample. However, bias tests do not work this way. They are tests of the population, namely the population of all of the studies that could be retrieved that tested a common hypothesis (e.g., all handgrip studies of ego-depletion). Maybe more studies exist than are available. Maybe the results based on the available studies differ from results if all studies were available, but that is irrelevant. The question is only whether the available studies are biased or not. So, why do we even test for significance? That is a good question. The test for significance only tells us whether bias is merely a product of random chance or whether it was introduced by questionable research practices. However, even random bias is bias. If a set of studies reports only significant results, and the observed power of the studies is only 70%, there is a discrepancy. If this discrepancy is not statistically significant, there is still a discrepancy. If it is statistically significant, we are allowed to attribute it to questionable research practices such as those that Baumeister and several others admitted using.

“We did run multiple studies, some of which did not work, and some of which worked better than others. You may think that not reporting the less successful studies is wrong, but that is how the field works.” (Roy Baumeister, personal email communication) (Schimmack, 2014).

Given the widespread use of questionable research practices in experimental social psychology, it is not surprising that bias-tests reveal bias. It is actually more surprising when these tests fail to reveal bias, which is most likely a problem of low statistical power (Renkewitz & Keiner, 2019).

Misunderstanding Power

The claims about power are not based on clearly defined constructs in statistics. Statistical power is a function of the strength of a signal (the population effect size) and the amount of noise (sampling error). Researches skills are not a part of statistical power. Results should be independent of a researcher. A researcher could of course pick procedures that maximize a signal (powerful interventions) or reduce sampling error (e.g., pre-post designs), but these factors play a role in the designing of a study. Once a study is carried out, the population effect size is what it was and the sampling error is what it was. Thus, honestly reported test statistics tell us about the signal-to-noise ratio in a study that was conducted. Skillful researchers would produce stronger test-statistics (higher t-values, F-values) than unskilled researchers. The problem for Baumeister and other ego-depletion researchers is that the t-values and F-values tend to be weak and suggest questionable research practices rather than skill produced significant results. In short, meta-analysis of test-statistics reveal whether researchers used skill or questionable research practices to produce significant results.

The reference to Morey (2013) suggests that there is a valid criticism of bias tests, but that is not the case. Power-based bias tests are based on sound statistical principles that were outlined by a statistician in the journal American Statistician (Sterling, Rosenbaum, & Weinkam, 1995). Building on this work, Jerry Brunner (professor of statistics) and I published theorems that provide the basis of bias tests like TES to reveal the use of questionable research practices (Brunner & Schimmack, 2019). The real challenge for bias tests is to estimate mean power without information about the population effect sizes. In this regard, TES is extremely conservative because it relies on a meta-analysis of observed effect sizes to estimate power. These effect sizes are inflated when questionable research practices were used, which makes the test conservative. However, there is a problem with TES when effect sizes are heterogeneous. This problem is avoided by alternative bias tests like the R-Index that I used to demonstrate publication bias in the handgrip studies of ego-depletion. In sum, bias tests like the R-Index and TES are based on solid mathematical foundations and simulation studies show that they work well in detecting the use of questionable research practices.

Confusing Absence of Evidence with Evidence of Absence

PET and PEESE are extension of Eggert’s regression test of publication bias. All methods relate sample sizes (or sampling error) to effect size estimates. Questionable research practices tend to introduce a negative correlation between sample size and effect sizes or a positive correlation between sampling error and effect sizes. The reason is that significance requires a signal to noise ratio of 2:1 for t-tests or 4:1 for F-tests to produce a significant result. To achieve this ratio with more noise (smaller sample, more sampling error), the signal has to be inflated more.

The novel contribution of PET and PEESE was to use the intercept of the regression model as an effect size estimate that corrects for publication bias. This estimate needs to be interpreted in the context of the sampling error of the regression model, using a 95%CI around the point estimate.

Carter et al. (2015) found that the 95%CI often included a value of zero, which implies that the data are too weak to reject the null-hypothesis. Such non-significant results are notoriously difficult to interpret because they neither support nor refute the null-hypothesis. The main conclusion that can be drawn from this finding is that the existing data are inconclusive.

This main conclusion does not change when the number of studies is less than 20. Stanley and Doucouliagos (2014) were commenting on the trustworthiness of point estimates and confidence intervals in smaller samples. Smaller samples introduce more uncertainty and we should be cautious in the interpretation of results that suggest there is an effect because the assumptions of the model are violated. However, if the results already show that there is no evidence, small samples merely further increase uncertainty and make the existing evidence even less conclusive.

Aside from the issues regarding the interpretation of the intercept, Cunningham and Baumeister also fail to address the finding that sample sizes and effect sizes were negatively correlated. If this negative correlation is not caused by questionable research practices, it must be caused by something else. Cunningham and Baumeister fail to provide an answer to this important question.

No Evidence of Flair and Skill

Earlier Cunningham and Baumeister (2016) claimed that power depends on researchers’ skills and they argue that new investigators may be less skilled than the experts who developed paradigms like Baumeister and colleagues.

However, they then point out that Carter et al.’s (2015) examined lab as a moderator and found no difference between studies conducted by Baumeister and colleagues or other laboratories.

Thus, there is no evidence whatsoever that Baumeister and colleagues were more skillful and produced more credible evidence for ego-depletion than other laboratories. The fact that everybody got ego-depletion effects can be attributed to the widespread use of questionable research practices that made it possible to get significant results even for implausible phenomena like extrasensory perception (John et al., 2012; Schimmack, 2012). Thus, the large number of studies that support ego-depletion merely shows that everybody used questionable research practices like Baumeister did (Schimmack, 2014; Schimmack, 2016), which is also true for many other areas of research in experimental social psychology (Schimmack, 2019). Francis (2014) found that 80% of articles showed evidence that QRPs were used.

Handgrip Replicability Analysis

The meta-analysis included 18 effect sizes based on handgrip studies.   Two unpublished studies (Ns = 24, 37) were not included in this analysis.   Seeley & Gardner (2003)’s study was excluded because it failed to use a pre-post design, which could explain the non-significant result. The meta-analysis reported two effect sizes for this study. Thus, 4 effects were excluded and the analysis below is based on the remaining 14 studies.

All articles presented significant effects of will-power manipulations on handgrip performance. Bray et al. (2008) reported three tests; one was deemed not significant (p = .10), one marginally significant (.06), and one was significant at p = .05 (p = .01). The results from the lowest p-value were used. As a result, the success rate was 100%.

Median observed power was 63%. The inflation rate is 37% and the R-Index is 26%. An R-Index of 22% is consistent with a scenario in which the null-hypothesis is true and all reported findings are type-I errors. Thus, the R-Index supports Carter and McCullough’s (2014) conclusion that the existing evidence does not provide empirical support for the hypothesis that will-power manipulations lower performance on a measure of will-power.

The R-Index can also be used to examine whether a subset of studies provides some evidence for the will-power hypothesis, but that this evidence is masked by the noise generated by underpowered studies with small samples. Only 7 studies had samples with more than 50 participants. The R-Index for these studies remained low (20%). Only two studies had samples with 80 or more participants. The R-Index for these studies increased to 40%, which is still insufficient to estimate an unbiased effect size.

One reason for the weak results is that several studies used weak manipulations of will-power (e.g., sniffing alcohol vs. sniffing water in the control condition). The R-Index of individual studies shows two studies with strong results (R-Index > 80). One study used a physical manipulation (standing one leg). This manipulation may lower handgrip performance, but this effect may not reflect an influence on will-power. The other study used a mentally taxing (and boring) task that is not physically taxing as well, namely crossing out “e”s. This task seems promising for a replication study.

Power analysis with an effect size of d = .2 suggests that a serious empirical test of the will-power hypothesis requires a sample size of N = 300 (150 per cell) to have 80% power in a pre-post study of will-power.

HandgripRindex

Conclusion

Baumeister has lost any credibility as a scientist. He is pretending to engage in a scientific dispute about the validity of ego-depletion research, but he is ignoring the most obvious evidence that has accumulated during the past decade. Social psychologists have misused the scientific method and engaged in a silly game of producing significant p-values that support their claims. Data were never used to test predictions and studies that failed to support hypotheses were not published.

“We did run multiple studies, some of which did not work, and some of which worked better than others. You may think that not reporting the less successful studies is wrong, but that is how the field works.” (Roy Baumeister, personal email communication)

As a result, the published record lacks credibility and cannot be used to provide empirical evidence for scientific claims. Ego-depletion is a glaring example of everything that went wrong in experimental social psychology. This is not surprising because Baumeister and his students used questionable research practices more than other social psychologists (Schimmack, 2018). Now he is trying to to repress this truth, which should not surprise any psychologist familiar with motivated biases and repressive coping. However, scientific journals should not publish his pathetic attempts to dismiss criticism of his work. Cunningham and Baumeister’s article provides not a single valid scientific argument. Frontiers of Psychology should retract the article.

References

Carter,E.C.,Kofler,L.M.,Forster,D.E.,and McCulloch,M.E. (2015).A series of meta-analytic tests of the depletion effect: Self-control does not seem to rely on a limited resource. J. Exp.Psychol.Gen. 144, 796–815. doi:10.1037/xge0000083

Francis’s Audit of Multiple-Study Articles in Psychological Science in 2009-2012

Citation: Francis G., (2014). The frequency of excess success for articles
in Psychological Science. Psychon Bull Rev (2014) 21:1180–1187
DOI 10.3758/s13423-014-0601-x

Introduction

The Open Science Collaboration article in Science has over 1,000 articles (OSC, 2015). It showed that attempting to replicate results published in 2008 in three journals, including Psychological Science, produced more failures than successes (37% success rate). It also showed that failures outnumbered successes 3:1 in social psychology. It did not show or explain why most social psychological studies failed to replicate.

Since 2015 numerous explanations have been offered for the discovery that most published results in social psychology cannot be replicated: decline effect (Schooler), regression to the mean (Fiedler), incompetent replicators (Gilbert), sabotaging replication studies (Strack), contextual sensitivity (vanBavel). Although these explanations are different, they share two common elements, (a) they are not supported by evidence, and (b) they are false.

A number of articles have proposed that the low replicability of results in social psychology are caused by questionable research practices (John et al., 2012). Accordingly, social psychologists often investigate small effects in between-subject experiments with small samples that have large sampling error. A low signal to noise ratio (effect size/sampling error) implies that these studies have a low probability of producing a significant result (i.e., low power and high type-II error probability). To boost power, researchers use a number of questionable research practices that inflate effect sizes. Thus, the published results provide the false impression that effect sizes are large and results are replicated, but actual replication attempts show that the effect sizes were inflated. The replicability projected suggested that effect sizes are inflated by 100% (OSC, 2015).

In an important article, Francis (2014) provided clear evidence for the widespread use of questionable research practices for articles published from 2009-2012 (pre crisis) in the journal Psychological Science. However, because this evidence does not fit the narrative that social psychology was a normal and honest science, this article is often omitted from review articles, like Nelson et al’s (2018) ‘Psychology’s Renaissance’ that claims social psychologists never omitted non-significant results from publications (cf. Schimmack, 2019). Omitting disconfirming evidence from literature reviews is just another sign of questionable research practices that priorities self-interest over truth. Given the influence that Annual Review articles hold, many readers maybe unfamiliar with Francis’s important article that shows why replication attempts of articles published in Psychological Science often fail.

Francis (2014) “The frequency of excess success for articles in Psychological Science”

Francis (2014) used a statistical test to examine whether researchers used questionable research practices (QRPs). The test relies on the observation that the success rate (percentage of significant results) should match the mean power of studies in the long run (Brunner & Schimmack, 2019; Ioannidis, J. P. A., & Trikalinos, T. A., 2007; Schimmack, 2012; Sterling et al., 1995). Statistical tests rely on the observed or post-hoc power as an estimate of true power. Thus, mean observed power is an estimate of the expected number of successes that can be compared to the actual success rate in an article.

It has been known for a long time that the actual success rate in psychology articles is surprisingly high (Sterling, 1995). The success rate for multiple-study articles is often 100%. That is, psychologists rarely report studies where they made a prediction and the study returns a non-significant results. Some social psychologists even explicitly stated that it is common practice not to report these ‘uninformative’ studies (cf. Schimmack, 2019).

A success rate of 100% implies that studies required 99.9999% power (power is never 100%) to produce this result. It is unlikely that many studies published in psychological science have the high signal-to-noise ratios to justify these success rates. Indeed, when Francis applied his bias detection method to 44 studies that had sufficient results to use it, he found that 82 % (36 out of 44) of these articles showed positive signs that questionable research practices were used with a 10% error rate. That is, his method could at most produce 5 significant results by chance alone, but he found 36 significant results, indicating the use of questionable research practices. Moreover, this does not mean that the remaining 8 articles did not use questionable research practices. With only four studies, the test has modest power to detect questionable research practices when the bias is relatively small. Thus, the main conclusion is that most if not all multiple-study articles published in Psychological Science used questionable research practices to inflate effect sizes. As these inflated effect sizes cannot be reproduced, the effect sizes in replication studies will be lower and the signal-to-noise ratio will be smaller, producing non-significant results. It was known that this could happen since 1959 (Sterling, 1959). However, the replicability project showed that it does happen (OSC, 2015) and Francis (2014) showed that excessive use of questionable research practices provides a plausible explanation for these replication failures. No review of the replication crisis is complete and honest, without mentioning this fact.

Limitations and Extension

One limitation of Francis’s approach and similar approaches like my incredibility Index (Schimmack, 2012) is that p-values are based on two pieces of information, the effect size and sampling error (signal/noise ratio). This means that these tests can provide evidence for the use of questionable research practices, when the number of studies is large, and the effect size is small. It is well-known that p-values are more informative when they are accompanied by information about effect sizes. That is, it is not only important to know that questionable research practices were used, but also how much these questionable practices inflated effect sizes. Knowledge about the amount of inflation would also make it possible to estimate the true power of studies and use it as a predictor of the success rate in actual replication studies. Jerry Brunner and I have been working on a statistical method that is able to to this, called z-curve, and we validated the method with simulation studies (Brunner & Schimmack, 2019).

I coded the 195 studies in the 44 articles analyzed by Francis and subjected the results to a z-curve analysis. The results are shocking and much worse than the results for the studies in the replicability project that produced an expected replication rate of 61%. In contrast, the expected replication rate for multiple-study articles in Psychological Science is only 16%. Moreover, given the fairly large number of studies, the 95% confidence interval around this estimate is relatively narrow and includes 5% (chance level) and a maximum of 25%.

There is also clear evidence that QRPs were used in many, if not all, articles. Visual inspection shows a steep drop at the level of significance, and the only results that are not significant with p < .05 are results that are marginally significant with p < .10. Thus, the observed discovery rate of 93% is an underestimation and the articles claimed an amazing success rate of 100%.

Correcting for bias, the expected discovery rate is only 6%, which is just shy of 5%, which would imply that all published results are false positives. The upper limit for the 95% confidence interval around this estimate is 14, which would imply that for every published significant result there are 6 studies with non-significant results if file-drawring were the only QRP that was used. Thus, we see not only that most article reported results that were obtained with QRPs, we also see that massive use of QRPs was needed because many studies had very low power to produce significant results without QRPs.

Conclusion

Social psychologists have used QRPs to produce impressive results that suggest all studies that tested a theory confirmed predictions. These results are not real. Like a magic show they give the impression that something amazing happened, when it is all smoke and mirrors. In reality, social psychologists never tested their theories because they simply failed to report results when the data did not support their predictions. This is not science. The 2010s have revealed that social psychological results in journals and text books cannot be trusted and that influential results cannot be replicated when the data are allowed to speak. Thus, for the most part, social psychology has not been an empirical science that used the scientific method to test and refine theories based on empirical evidence. The major discovery in the 2010s was to reveal this fact, and Francis’s analysis provided valuable evidence to reveal this fact. However, most social psychologists preferred to ignore this evidence. As Popper pointed out, this makes them truly ignorant, which he defined as “the unwillingness to acquire knowledge.” Unfortunately, even social psychologists who are trying to improve it wilfully ignore Francis’s evidence that makes replication failures predictable and undermines the value of actual replication studies. Given the extent of QRPs, a more rational approach would be to dismiss all evidence that was published before 2012 and to invest resources in new research with open science practices. Actual replication failures were needed to confirm predictions made by bias tests that old studies cannot be trusted. The next decade should focus on using open science practices to produce robust and replicable findings that can provide the foundation for theories.

The Diminishing Utility of Replication Studies In Social Psychology

Dorthy Bishop writes on her blog.

“As was evident from my questions after the talk, I was less enthused by the idea of doing a large, replication of Darryl Bem’s studies on extra-sensory perception. Zoltán Kekecs and his team have put in a huge amount of work to ensure that this study meets the highest standards of rigour, and it is a model of collaborative planning, ensuring input into the research questions and design from those with very different prior beliefs. I just wondered what the point was. If you want to put in all that time, money and effort, wouldn’t it be better to investigate a hypothesis about something that doesn’t contradict the laws of physics?”


I think she makes a valid and important point. Bem’s (2011) article highlighted everything that was wrong with the research practices in social psychology. Other articles in JPSP are equally incredible, but this was ignored because naive readers found the claims more plausible (e.g., blood glucose is the energy for will power). We know now that none of these published results provide empirical evidence because the results were obtained with questionable research practices (Schimmack, 2014; Schimmack, 2018). It is also clear that these were not isolated incidents, but that hiding results that do not support a theory was (and still is) a common practice in social psychology (John et al., 2012; Schimmack, 2019).

A large attempt at estimating the replicability of social psychology revealed that only 25% of published significant results could be replicated (OSC). The rate for between-subject experiments was even lower. Thus, the a-priori probability (base rate) that a randomly drawn study from social psychology will produce a significant result in a replication attempt is well below 50%. In other words, a replication failure is the more likely outcome.

The low success rate of these replication studies was a shock. However, it is sometimes falsely implied that the low replicability of results in social psychology was not recognized earlier because nobody conducted replication studies. This is simply wrong. In fact, social psychology is one of the disciplines in psychology that required researchers to conduct multiple studies that showed the same effect to ensure that a result was not a false positive result. Bem had to present 9 studies with significant results to publish his crazy claims about extrasensory perception (Schimmack, 2012). Most of the studies that failed to replicate in the OSC replication project were taken from multiple-study articles that reported several successful demonstrations of an effect. Thus, the problem in social psychology was not that nobody conducted replication studies. The problem was that social psychologists only reported replication studies that were successful.

The proper analyses of the problem also suggests a different solution to the problem. If we pretend that nobody did replication studies, it may seem useful to starting doing replication studies. However, if social psychologists conducted replication studies, but did not report replication failures, the solution is simply to demand that social psychologists report all of their results honestly. This demand is so obvious that undergraduate students are surprised when I tell them that this is not the way social psychologists conduct their research.

In sum, it has become apparent that questionable research practices undermine the credibility of the empirical results in social psychology journals, and that the majority of published results cannot be replicated. Thus, social psychology lacks a solid empirical foundation.

What Next?

It is implied by information theory that little information is gained by conducting actual replication studies in social psychology because a failure to replicate the original result is likely and uninformative. In fact, social psychologists have responded to replication failures by claiming that these studies were poorly conducted and do not invalidate the original claims. Thus, replication studies are both costly and have not advanced theory development in social psychology. More replication studies are unlikely to change this.

A better solution to the replication crisis in social psychology is to characterize research in social psychology from Festinger’s classic small-sample, between-subject study in 1957 to research in 2017 as exploratory and hypotheses generating research. As Bem suggested to his colleagues, this was a period of adventure and exploration where it was ok to “err on the side of discovery” (i.e., publish false positive results, like Bem’s precognition for erotica). Lot’s of interesting discoveries were made during this period; it is just not clear which of these findings can be replicated and what they tell us about social behavior.

Thus, new studies in social psychology should not try to replicate old studies. For example, nobody should try to replicate Devine’s subliminal priming study with racial primes with computers and software from the 1980s (Devine, 1989). Instead, prominent theoretical predictions should be tested with the best research methods that are currently available. Thus, the way forward is not to do more replication studies, but rather to use open science (a.k.a. honest science) that uses experiments to subject theories to empirical tests that may also falsify a theory (e.g., subliminal racial stimuli have no influence on behavior). The main shift that is required is to get away from research that can only confirm theories and to allow for empirical data to falsify theories.

This was exactly the intent of Danny Kahneman’s letter, when he challenged social priming researchers to respond to criticism of their work by going into their labs and to demonstrate that these effects can be replicated across many labs.

Kahneman makes it clear that the onus of replication is on the original researchers who want others to believe their claims. The response to this letter speaks volumes. Not only did social psychologists fail to provide new and credible evidence that their results can be replicated, they also demonstrated defiant denial in the face of replication failures by others. The defiant denial by prominent social psychologists (e.g., Baumeister, 2019) make it clear that they will not be convinced by empirical evidence, while others who can look at the evidence objectively do not need more evidence to realize that the social psychological literature is a train-wreck (Schimmack, 2017; Kahneman, 2017). Thus, I suggest that young social psychologists search the train wreck for survivors, but do not waste their time and resources on replication studies that are likely to fail.

A simple guide through the wreckage of social psychology is to distrust any significant result with a p-value greater than .01 (Schimmack, 2019). Prediction markets also suggest that readers are able to distinguish credible and incredible results (Atlantic). Thus, I recommend to build on studies that are credible and to stay clear of sexy findings that are unlikely to replicate. As Danny Kahneman pointed out, young social psychologists who work in questionable areas face a dilemma. Either they have to replicate the questionable methods that were used to get the original results, which is increasingly considered unethical, or they end up with results that are not very informative. On the positive side, the replication crisis implies that there are many important topics in social psychology that need to be studied properly with the scientific method. Addressing these important questions may be the best way to rescue social psychology.

Fact-Checking Roy Baumeister

Roy Baumeister wrote a book chapter with the title “Self-Control, Ego Depletion, and Social Psychology’s Replication CrisisRoy” (preprint). I think this chapter will make a valuable contribution to the history of psychology and provides valuable insights into the minds of social psychologists.

I fact-checked the chapter and comment on 31 misleading or false statements.

https://replicationindex.files.wordpress.com/2019/09/ego-depletion-and-replication-crisis.docx

Comments are welcome.

Estimating the Replicability of Psychological Science

Over the past years, psychologists have become increasingly concerned about the credibility of published results. The credibility crisis started in 2011, when Bem published incredible results that seemed to suggest that humans can foresee random future events. Bem’s article revealed fundamental flaws in the way psychologists conduct research. The main problem is that psychology journals only publish statistically significant results (Sterling, 1959). If only significant results are published, all hypotheses will receive empirical support as long as they are tested. This is akin to saying that everybody has a 100% free throw average or nobody ever makes a mistake if we do not count failures.

The main problem of selection for significance is that we do not know the real strength of evidence that empirical studies provide. Maybe the selection effect is small and most studies would replicate. However, it is also possible that many studies might fail a replication test. Thus, the crisis of confidence is a crisis of uncertainty.

The Open Science Collaboration conducted actual replication studies to estimate the replicability of psychological science. They replicated 97 studies with statistically significant results and were able to reproduce 35 significant results (a 36% success rate). This is a shockingly low success rate. Based on this finding, most published results cannot be trusted, especially because there is heterogeneity across studies. Some studies would have an even lower chance of replication and several studies might even be outright false positives (there is actually no real effect).

As important as this project was to reveal major problems with the research culture in psychological science, there are also some limitations that cast doubt about the 36% estimate as a valid estimate of the replicability of psychological science. First, the sample size is small and sampling error alone might have lead to an underestimation of the replicability in the population of studies. However, sampling error could also have produced a positive bias. Another problem is that most of the studies focused on social psychology and that replicability in social psychology could be lower than in other fields. In fact, a moderator analysis suggested that the replication rate in cognitive psychology is 50%, while the replication rate in social psychology is only 25%. The replicated studies were also limited to a single year (2008) and three journals. It is possible that the replication rate has increased since 2008 or could be higher in other journals. Finally, there have been concerns about the quality of some of the replication studies. These limitations do not undermine the importance of the project, but they do imply that the 36% estimate is an estimate and that it may underestimate the replicability of psychological science.

Over the past years, I have been working on an alternative approach to estimate the replicability of psychological science. This approach starts with the simple fact that replicabiliity is tightly connected to the statistical power of a study because statistical power determines the long-run probability of producing significant results (Cohen, 1988). Thus, estimating statistical power provides valuable information about replicability. Cohen (1962) conducted a seminal study of statistical power in social psychology. He found that the average power to detect an average effect size was around 50%. This is the first estimate of replicability of psychological science, although it was only based on one journal and limited to social psychology. However, subsequent studies replicated Cohen’s findings and found similar results over time and across journals (Sedlmeier & Gigerenzer, 1989). It is noteworthy that the 36% estimate from the OSC project is not statistically different from Cohen’s estimate of 50%. Thus, there is convergent evidence that replicability in social psychology is around 50%.

In collaboration with Jerry Brunner, I have developed a new method that can estimate mean power for a set of studies that are selected for significance and that vary in effect sizes and samples sizes, which produces heterogeneity in power (Brunner & Schimmack, 2018). The input for this method are the actual test statistics of significance tests (e.g., t-tests, F-tests). These test-statistics are first converted into two-tailed p-values and then converted into absolute z-scores. The magnitude of these absolute z-scores provides information about the strength of evidence against the null-hypotheses. The histogram of these z-scores, called a z-curve, is then used to fit a finite mixture model to the data that estimates mean power, while taking selection for significance intro account. Extensive simulation studies demonstrate that z-curve performs well and provides better estimates than alternative methods. Thus, z-curve is the method of choice for estimating the replicability of psychological science on the basis of the test statistics that are reported in original articles.

For this blog post, I am reporting results based on preliminary results from a large project that extracts focal hypothesis from a broad range of journals that cover all areas of psychology for the years 2010 to 2017. The hand-coding of these articles complements a similar project that relies on automatic extraction of test statistics (Schimmack, 2018).

Table 1 shows the journals that have been coded so far. It also shows the estimates based on the automated method and for hand-coding of focal hypotheses.

JournalHandAutomated
Psychophysiology8475
Journal of Abnormal Psychology7668
Journal of Cross-Cultural Psychology7377
Journal of Research in Personality6875
J. Exp. Psych: Learning, Memory, & Cognition5877
Journal of Experimental Social Psychology5562
Infancy5368
Behavioral Neuroscience5368
Psychological Science5266
JPSP-Interpersonal Relations & Group Processes3363
JPSP-Attitudes and Social Cognition3065
Mean5869

Hand coding of focal hypothesis produces lower estimates than the automated method because the automated analysis also codes manipulation checks and other highly significant results that are not theoretically important. The correlation between the two methods shows consistency across the two methods, r = .67. Finally, the mean for the automated method, 69%, is close to the mean for over 100 journals, 72%, suggesting that the sample of journals is an unbiased sample.

The hand coding results also confirm results found with the automated method that social psychology has a lower replicability than some other disciplines. Thus, the OSC reproducibility results that are largely based on social psychology should not be used to make claims about psychological science in general.

The figure below shows the output of the latest version of z-curve. The first finding is that the replicability estimate for all 1,671 focal tests is 56% with a relatively tight confidence interval ranging from 45% to 56%. ZZZ The next finding is that the discovery rate or success rate is 92%, using p < .05 as the criterion. This confirms that psychology journals continue to published results are selected for significance (Sterling, 1959). The histogram further shows that even more results would be significant if p-values below .10 are included as evidence for “marginal significance.”

Z-Curve.19.1 also provides an estimate of the size of the file drawer. It does so by projecting the distribution of observed significant results into the range of non-significant results (grey curve). The file drawer ratio shows that for every published result, we would expect roughly two unpublished studies with non-significant results. However, z-curve cannot distinguish between different questionable research practices. Rather than not disclosing failed studies researchers may not disclose other statistical analyses within a published study to report significant results.

Z-Curve.19.1 also provides an estimate of the false positive rate (FDR). FDR is the percentage of significant results that may arise from testing a true nil-hypothesis, where the population effect size is zero. For a long time, the consensus has been that false positives are rare because the nil-hypothesis is rarely true (Cohen, 1994). Consistent with this view, Soric’s estimate of the maximum false discovery rate is only 10% with a tight CI ranging from 8% to 16%.

However, the focus on the nil-hypothesis is misguided because it treats tiny deviations from zero as true hypotheses even if the effect size has no practical or theoretical significance. These effect sizes also lead to low power and replication failures. Therefore, Z-Curve 19.1 also provides an estimate of the FDR that treats studies with very low power as false positives. This broader definition of false positives raises the FDR estimate slightly, but 15% is still a low percentage. Thus, the modest replicability of results in psychological science is mostly due to low statistical power to detect true effects rather than a high number of false positive discoveries.

The reproducibility project showed that studies with low p-values were more likely to replicate. This relationship follows from the influence of statistical power on p-values and replication rates. To achieve a replication rate of 80%, p-values had to be less than .00005 or the z-score had to exceed 4 standard deviations. However, this estimate was based on a very small sample of studies. Z-Curve.19.1 also provides estimates of replicability for different levels of evidence. These values are shown below the x-axis. Consistent with the OSC results, a replication rate over 80% is only expected once z-scores are greater than 4.

The results also provide information about the choice of the alpha criterion to draw inferences from significance tests in psychology. To do so, it is important to distinguish observed p-values and type-I probabilities. For a single unbiased tests, we can infer from an observed p-value less than .05 that the risk of a false positive result is less than 5%. However, when multiple comparisons are made or results are selected for significance, an observed p-values less than .05 does not imply that the type-I error risk is below .05. To claim a type-I error risk of 5% or less, we have to correct the observed p-values, just like a Bonferroni correction. As 50% power corresponds to statistical significance, we see that z-scores between 2 and 3 are not statistically significant; that is, the type-I error risk is greater than 5%. Thus, the standard criterion to claim significance with alpha = .05 is a p-value of .003. Given the popularity of .005, I suggest to use p = .005 as a criterion for statistical significance. However, this claim is not based on lowering the criterion for statistical significance because p < .005 still only allows to claim that the type-I error probability is less than 5%. The need for a lower criterion value stems from the inflation of the type-I error rate due to selection for significance. This is a novel argument that has been overlooked in the significance wars, which ignored the influence of publication bias on false positive risks.

Finally, z-curve.19.1 makes it possible to examine the robustness of the estimates by using different selection criteria. One problem with selection models is that p-values just below .05, say in the .01 to .05 range, can arise from various questionable research practices that have different effects on replicability estimates. To address this problem, it is possible to estimate the density with a different selection criterion, while still estimating the replicability with alpha = .05 as the criterion. Figure 2 shows the results by using only z-scores greater than 2.5, p = .012) to fit the observed z-curve for z-scores greater than 2.5.

The blue dashed line at z = 2.5 shows the selection criterion. The grey curve between 1.96 and 2.5 is projected form the distribution for z-scores greater than 2.5. Results show a close fit with the observed distribution. A s a result, the parameter estimates are also very similar. Thus, the results are robust and the selection model seems to be reasonable.

Conclusion

Psychology is in a crisis of confidence about the credibility of published results. The fundamental problems are as old as psychology itself. Psychologists have conducted low powered studies and selected only studies that worked for decades (Cohen, 1962; Sterling, 1959). However, awareness of these problems has increased in recent years. Like many crises, the confidence crisis in psychology has created confusion. Psychologists are aware that there is a problem, but they do not know how large the problem is. Some psychologists believe that there is no crisis and pretend that most published results can be trusted. Others are worried that most published results are false positives. Meta-psychologists aim to reduce the confusion among psychologists by applying the scientific method to psychological science itself.

This blog post provided the most comprehensive assessment of the replicability of psychological science so far. The evidence is largely consistent with previous meta-psychological investigations. First, replicability is estimated to be slightly above 50%. However, replicability varies across discipline and the replicability of social psychology is below 50%. The fear that most published results are false positives is not supported by the data. Replicability increases with the strength of evidence against the null-hypothesis. If the p-value is below .00001, studies are likely to replicate. However, significant results with p-values above .005 should not be considered statistically significant with an alpha level of 5%, because selection for significance inflates the type-I error. Only studies with p < .005 can claim statistical significance with alpha = .05.

The correction for publication bias implies that researchers have to increase sample sizes to meet the more stringent p < .005 criterion. However, a better strategy is to preregister studies to ensure that reported results can be trusted. In this case, p-values below .05 are sufficient to demonstrate statistical significance with alpha = .05. Given the low prevalence of false positives in psychology, I do see no need to lower the alpha criterion.

Future Directions

This blog post is just an interim report. The final project requires hand-coding of a broader range of journals. Readers who think that estimating the replicability of psychological science is beneficial and who want information about a particular journal are invited to collaborate on this project and can obtain authorship if their contribution is substantial enough to warrant authorship. Please consider taking part in this project. Although it is a substantial time commitment, it doesn’t require participants or materials that are needed for actual replication studies. Please consider taking part in this project. Contact me, if you are interested and want to know how you can get involved.