Tag Archives: Statistical 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).


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.


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.


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.


Post-Hoc-Power Curves of Social Psychology in Psychological Science, JESP, and Social Cognition

Post-hoc-power curves are used to evaluate the replicability of published results.  At present, PHP curves are based on t-tests and F-tests that are automatically extracted from text files of journal articles.  All test results are converted into z-scores.  PHP-curves are fitted to the density of the histogram of z-scores.

It is well known that non-significant results are less likely to be published and end up in the proverbial file-drawer.  To overcome this problem, PHP curves are fitted to the data by excluding non-significant results from the estimation of typical power (Simonsohn et al., 2013, 2014).

Another problem in the estimation of typical power is that power varies across tests. Heterogeneity of power leads to more variation in observed z-scores than a homogeneous model would assume (see comparison of variances in the figures below).  PHP-curves address this problem by fitting a model with multiple true power values to the observed data. Fit for the non-significant results is not expected to be good due to the file drawer problem. In fact, the gap between actual and predicted data can be considered a rough estimate of the size of the file-drawer.

For heterogeneous data, power depends on the set of results that is being analyzed. The reason is that low z-scores are more likely to be obtained in studies with low power, whereas high z-scores are more likely to be the result of high powered studies. The figures below estimated power for z-scores in the range from 2 to 6.  The mode of the red heterogenous curve shows that power for all tests would be considerably lower.  However, non-significant results are typically not interpreted or even excluded from published studies. Thus, replicability is better indexed by the typical power of significant results.

The power estimates for all JESP articles and for social psychology articles in Psychological Science are very similar (47%, and 45%). Power for Social Cognition in the years from 2010 to present is estimated to be higher (60%).  Older issues could not be analyzed because text recognition did not work.  In comparison, the estimated power for Memory related articles in Psychological Science is higher (66%).

The average can be a misleading statistic for skewed distributions. The figures show that the majority of significant results are closer to the lower limit (z = 2) than to the upper limit (z = 6) of the test interval. Thus, the median power is lower than the average power of 45-60%.

It is important to realize that post-hoc power is meaningful when it is based on a large set of studies.  A z-score of 4 is more likely to be based on a highly powered study than a z-score of 2, but a single z-score of 2 could be based on a high-powered study or it could be a type-I error. The purpose of PHP-curves is to evaluate journals, areas of research, and other meaningful sets of studies.  Hopefully, recent attempts to increase the replicability of social psychology will increase power.  PHP-curves, the R-Index, and estimates of typical power can be used to document improvements in future years.



A Critical Review of Cumming’s (2014) New Statistics: Reselling Old Statistics as New Statistics

Cumming (2014) wrote an article “The New Statistics: Why and How” that was published in the prestigious journal Psychological Science.   On his website, Cumming uses this article to promote his book “Cumming, G. (2012). Understanding The New Statistics: Effect Sizes, Confidence Intervals, and Meta-Analysis. New York: Routledge.”

The article clear states the conflict of interest. “The author declared that he earns royalties on his book (Cumming, 2012) that is referred to in this article.” Readers are therefore warned that the article may at least inadvertently give an overly positive account of the new statistics and an overly negative account of the old statistics. After all, why would anybody buy a book about new statistics when the old statistics are working just fine.

This blog post critically examines Cumming’s claim that his “new statistics” can solve endemic problems in psychological research that have created a replication crisis and that the old statistics are the cause of this crisis.

Like many other statisticians who are using the current replication crisis as an opportunity to sell their statistical approach, Cumming’s blames null-hypothesis significance testing (NHST) for the low credibility of research articles in Psychological Science (Francis, 2013).

In a nutshell, null-hypothesis significance testing entails 5 steps. First, researchers conduct a study that yields an observed effect size. Second, the sampling error of the design is estimated. Third, the ratio of the observed effect size and sampling error (signal-to-noise ratio) is computed to create a test-statistic (t, F, chi-square). The test-statistic is then used to compute the probability of obtaining the observed test-statistic or a larger one under the assumption that the true effect size in the population is zero (there is no effect or systematic relationship). The last step is to compare the test statistic to a criterion value. If the probability (p-value) is less than a criterion value (typically 5%), the null-hypothesis is rejected and it is concluded that an effect was present.

Cumming’s (2014) claims that we need a new way to analyze data because there is “renewed recognition of the severe flaws of null-hypothesis significance testing (NHST)” (p. 7). His new statistical approach has “no place for NHST” (p. 7). His advice is to “whenever possible, avoid using statistical significance or p values” (p. 8).

So what is wrong with NHST?

The first argument against NHST is that Ioannidis (2005) wrote an influential article with the eye-catching title “Why most published research findings are false” and most research articles use NHST to draw inferences from the observed results. Thus, NHST seems to be a flawed method because it produces mostly false results. The problem with this argument is that Ioannidis (2005) did not provide empirical evidence that most research findings are false, nor is this a particularly credible claim for all areas of science that use NHST, including partical physics.

The second argument against NHST is that researchers can use questionable research practices to produce significant results. This is not really a criticism of NHST, because researchers under pressure to publish are motivated to meet any criteria that are used to select articles for publication. A simple solution to this problem would be to publish all submitted articles in a single journal. As a result, there would be no competition for limited publication space in more prestigious journals. However, better studies would be cited more often and researchers will present their results in ways that lead to more citations. It is also difficult to see how psychology can improve its credibility by lowering standards for publication. A better solution would be to ensure that researchers are honestly reporting their results and report credible evidence that can provide a solid empirical foundation for theories of human behavior.

Cummings agrees. “To ensure integrity of the literature, we must report all research conducted to a reasonable standard, and reporting must be full and accurate” (p. 9). If a researcher conducted five studies with only a 20% chance to get a significant result and would honestly report all five studies, p-values would provide meaningful evidence about the strength of the evidence, namely most p-values would be non-significant and show that the evidence is weak. Moreover, post-hoc power analysis would reveal that the studies had indeed low power to test a theoretical prediction. Thus, I agree with Cumming’s that honesty and research integrity are important, but I see no reason to abandon NHST as a systematic way to draw inferences from a sample about the population because researchers have failed to disclose non-significant results in the past.

Cumming’s then cites a chapter by Kline (2014) that “provided an excellent summary of the deep flaws in NHST and how we use it” (p. 11). Apparently, the summary is so excellent that readers are better off by reading the actual chapter because Cumming’s does not explain what these deep flaws are. He then observes that “very few defenses of NHST have been attempted” (p. 11). He doesn’t even list a single reference. Here is one by a statistician: “In defence of p-values” (Murtaugh, 2014). In a response, Gelman agrees that the problem is more with the way p-values are used rather than with the p-value and NHST per se.

Cumming’s then states a single problem of NHST. Namely that it forces researchers to make a dichotomous decision. If the signal-to-noise ratio is above a criterion value, the null-hypothesis is rejected and it is concluded that an effect is present. If the signal-to-noise ratio is below the criterion value the null-hypothesis is not rejected. If Cumming’s has a problem with decision making, it would be possible to simply report the signal-to-noise ratio or simply to report the effect size that was observed in a sample. For example, mortality in an experimental Ebola drug trial was 90% in the control condition and 80% in the experimental condition. As this is the only evidence, it is not necessary to compute sampling error, signal-to-noise ratios, or p-values. Given all of the available evidence, the drug seems to improve survival rates. But wait. Now a dichotomous decision is made based on the observed mean difference and there is no information about the probability that the results in the drug trial generalize to the population. Maybe the finding was a chance finding and the drug actually increases mortality. Should we really make life-and-death decision if the decision were based on the fact that 8 out of 10 patients died in one condition and 9 out of 10 patients died in the other condition?

Even in a theoretical research context decisions have to be made. Editors need to decide whether they accept or reject a submitted manuscript and readers of published studies need to decide whether they want to incorporate new theoretical claims in their theories or whether they want to conduct follow-up studies that build on a published finding. It may not be helpful to have a fixed 5% criterion, but some objective information about the probability of drawing the right or wrong conclusions seems useful.

Based on this rather unconvincing critique of p-values, Cumming’s (2014) recommends that “the best policy is, whenever possible, not to use NHST at all” (p. 12).

So what is better than NHST?

Cumming then explains how his new statistics overcome the flaws of NHST. The solution is simple. What is astonishing about this new statistic is that it uses the exact same components as NHST, namely the observed effect size and sampling error.

NHST uses the ratio of the effect size and sampling error. When the ratio reaches a value of 2, p-values reach the criterion value of .05 and are considered sufficient to reject the null-hypothesis.

The new statistical approach is to multiple the standard error by a factor of 2 and to add and subtract this value from the observed mean. The interval from the lower value to the higher value is called a confidence interval. The factor of 2 was chosen to obtain a 95% confidence interval.  However, drawing a confidence interval alone is not sufficient to draw conclusions from the data. Whether we describe the results in terms of a ratio, .5/.2 = 2.5 or in terms of a 95%CI = .5 +/- .2 or CI = .1 to .7, is not a qualitative difference. It is simply different ways to provide information about the effect size and sampling error. Moreover, it is arbitrary to multiply the standard error by a factor of 2. It would also be possible to multiply it by a factor of 1, 3, or 5. A factor of 2 is used to obtain a 95% confidence interval rather than a 20%, 50%, 80%, or 99% confidence interval. A 95% confidence is commonly used because it corresponds to a 5% error rate (100 – 95 = 5!). A 95% confidence interval is as arbitrary as a p-value of .05.

So, how can a p-value be fundamentally wrong and how can a confidence interval be the solution to all problems if they provide the same information about effect size and sampling error? In particular how do confidence intervals solve the main problem of making inferences from an observed mean in a sample about the mean in a population?

To sell confidence intervals, Cumming’s uses a seductive example.

“I suggest that, once freed from the requirement to report p values, we may appreciate how simple, natural, and informative it is to report that “support for Proposition X is 53%, with a 95% CI of [51, 55],” and then interpret those point and interval estimates in practical terms” (p 14).

Support for proposition X is a rather unusual dependent variable in psychology. However, let us assume that Cumming refers to an opinion poll among psychologists whether NHST should be abandoned. The response format is a simple yes/no format. The average in the sample is 53%. The null-hypothesis is 50%. The observed mean of 53% in the sample shows more responses in favor of the proposition. To compute a significance test or to compute a confidence interval, we need to know the standard error. The confidence interval ranges from 51% to 55%. As the 95% confidence interval is defined by the observed mean plus/minus two standard errors, it is easy to see that the standard error is SE = (53-51)/2 = 1% or .01. The formula for the standard error in a one sample test with a dichotomous dependent variable is sqrt(p * (p-1) / n)). Solving for n yields a sample size of N = 2,491. This is not surprising because public opinion polls often use large samples to predict election outcomes because small samples would not be informative. Thus, Cumming’s example shows how easy it is to draw inferences from confidence intervals when sample sizes are large and confidence intervals are tight. However, it is unrealistic to assume that psychologists can and will conduct every study with samples of N = 1,000. Thus, the real question is how useful confidence intervals are in a typical research context, when researchers do not have sufficient resources to collect data from hundreds of participants for a single hypothesis test.

For example, sampling error for a between-subject design with N = 100 (n = 50 per cell) is SE = 2 / sqrt(100) = .2. Thus, the lower and upper limit of the 95%CI are 4/10 of a standard deviation away from the observed mean and the full width of the confidence interval covers 8/10th of a standard deviation. If the true effect size is small to moderate (d = .3) and a researcher happens to obtain the true effect size in a sample, the confidence interval would range from d = -.1 to d = .7. Does this result support the presence of a positive effect in the population? Should this finding be published? Should this finding be reported in newspaper articles as evidence for a positive effect? To answer this question, it is necessary to have a decision criterion.

One way to answer this question is to compute the signal-to-noise ratio, .3/.2 = 1.5 and to compute the probability that the positive effect in the sample could have occurred just by chance, t(98) = .3/.2 = 1.5, p = .15 (two-tailed). Given this probability, we might want to see stronger evidence. Moreover, a researcher is unlikely to be happy with this result. Evidently, it would have been better to conduct a study that could have provided stronger evidence for the predicted effect, say a confidence interval of d = .25 to .35, but that would have required a sample size of N = 6,500 participants.

A wide confidence interval can also suggest that more evidence is needed, but the important question is how much more evidence is needed and how narrow a confidence interval should be before it can give confidence in a result. NHST provides a simple answer to this question. The evidence should be strong enough to reject the null-hypothesis with a specified error rate. Cumming’s new statistics provides no answer to the important question. The new statistics is descriptive, whereas NHST is an inferential statistic. As long as researchers merely want to describe their data, they can report their results in several ways, including reporting of confidence intervals, but when they want to draw conclusions from their data to support theoretical claims, it is necessary to specify what information constitutes sufficient empirical evidence.

One solution to this dilemma is to use confidence intervals to test the null-hypothesis. If the 95% confidence interval does not include 0, the ratio of effect size / sampling error is greater than 2 and the p-value would be less than .05. This is the main reason why many statistics programs report 95%CI intervals rather than 33%CI or 66%CI. However, the use of 95% confidence intervals to test significance is hardly a new statistical approach that justifies the proclamation of a new statistic that will save empirical scientists from NHST. It is NHST! Not surprisingly, Cumming’s states that “this is my least preferred way to interpret a confidence interval” (p. 17).

However, he does not explain how researchers should interpret a 95% confidence interval that does include zero. Instead, he thinks it is not necessary to make a decision. “We should not lapse back into dichotomous thinking by attaching any particular importance to whether a value of interest lies just inside or just outside our CI.”

Does an experimental treatment for Ebolay work? CI = -.3 to .8. Let’s try it. Let’s do nothing and do more studies forever. The benefit of avoiding making any decisions is that one can never make a mistake. The cost is that one can also never claim that an empirical claim is supported by evidence. Anybody who is worried about dichotomous thinking might ponder the fact that modern information processing is built on the simple dichotomy of 0/1 bits of information and that it is common practice to decide the fate of undergraduate students on the basis of scoring multiple choice tests in terms of True or False answers.

In my opinion, the solution to the credibility crisis in psychology is not to move away from dichotomous thinking, but to obtain better data that provide more conclusive evidence about theoretical predictions and a simple solution to this problem is to reduce sampling error. As sampling error decreases, confidence intervals get smaller and are less likely to include zero when an effect is present and the signal-to-noise ratio increases so that p-values get smaller and smaller when an effect is present. Thus, less sampling error also means less decision errors.

The question is how small should sampling error be to reduce decision error and at what point are resources being wasted because the signal-to-noise ratio is clear enough to make a decision.

Power Analysis

Cumming’s does not distinguish between Fischer’s and Neyman-Pearson’s use of p-values. The main difference is that Fischer advocated the use of p-values without strict criterion values for significance testing. This approach would treat p-values just like confidence intervals as continuous statistics that do not imply an inference. A p-value of .03 is significant with a criterion value of .05, but it is not significant with a criterion value of .01.

Neyman-Pearson introduced the concept of a fixed criterion value to draw conclusions from observed data. A criterion value of p = .05 has a clear interpretation. It means that a test of 1,000 null-hypotheses is expected to produce about 50 significant results (type-I errors). A lower error rate can be achieved by lowering the criterion value (p < .01 or p < .001).

Importantly, Neyman-Pearson also considered the alternative problem that the p-value may fail to reach the critical value when an effect is actually present. They called this probability the type-II error. Unfortunately, social scientists have ignored this aspect of Neyman-Pearson Significance Testing (NPST). Researchers can avoid making type-II errors by reducing sampling error. The reason is that a reduction of sampling error increases the signal-to-noise ratio.

For example, the following p-values were obtained from simulating studies with 95% power. The graph only shows p-values greater than .001 to make the distribution of p-values more prominent. As a result 62.5% of the data are missing because these p-values are below p < .001. The histogram of p-values has been popularized by Simmonsohn et al. (2013) as a p-curve. The p-curve shows that p-values are heavily skewed towards low p-values. Thus, the studies provide consistent evidence that an effect is present, even though p-values can vary dramatically from one study (p = .0001) to the next (p = .02). The variability of p-values is not a problem for NPST as long as the p-values lead to the same conclusion because the magnitude of a p-value is not important in Neyman-Pearson hypothesis testing.


The next graph shows p-values for studies with 20% power. P-values vary just as much, but now the variation covers both sides of the significance criterion, p = .05. As a result, the evidence is often inconclusive and 80% of studies fail to reject the false null-hypothesis.


seed = length(“Cumming’sDancingP-Values”)
low_limit = .000
up_limit = .10
p <-(1-pnorm(rnorm(2500,qnorm(.975,0,1)+qnorm(.20,0,1),1),0,1))*2
percent_below_lower_limit = length(subset(p, p <  low_limit))/length(p)
If a study is designed to test a qualitative prediction (an experimental manipulation leads to an increase on an observed measure), power analysis can be used to plan a study so that it has a high probability of providing evidence for the hypothesis if the hypothesis is true. It does not matter whether the hypothesis is tested with p-values or with confidence intervals by showing that the confidence does not include zero.

Thus, power analysis seems useful even for the new statistics. However, Cummings is “ambivalent about statistical power” (p. 23). First, he argues that it has “no place when we use the new statistics” (p. 23), presumably because the new statistics never make dichotomous decisions.

Cumming’s next argument against power is that power is a function of the type-I error criterion. If the type-I error probability is set to 5% and power is only 33% (e.g., d = .5, between-group design N = 40), it is possible to increase power by increasing the type-I error probability. If type-I error rate is set to 50%, power is 80%. Cumming’s thinks that this is an argument against power as a statistical concept, but raising alpha to 50% is equivalent to reducing the width of the confidence interval by computing a 50% confidence interval rather than a 95% confidence interval. Moreover, researchers who adjust alpha to 50% are essentially saying that the null-hypothesis would produce a significant result in every other study. If an editor finds this acceptable and wants to publish the results, neither power analysis nor the reported results are problematic. It is true that there was a good chance to get a significant result when a moderate effect is present (d = .5, 80% probability) and when no effect is present (d = 0, 50% probability). Power analysis provides accurate information about the type-I and type-II error rates. In contrast, the new statistics provides no information about error rates in decision making because it is merely descriptive and does not make decisions.

Cumming then points out that “power calculations have traditionally been expected [by granting agencies], but these can be fudged” (p. 23). The problem with fudging power analysis is that the requested grant money may be sufficient to conduct the study, but insufficient to produce a significant result. For example, a researcher may be optimistic and expect a strong effect, d = .80, when the true effect size is only a small effect, d = .20. The researcher conducts a study with N = 52 participants to achieve 80% power. In reality the study has only 11% power and the researcher is likely to end up with a non-significant result. In the new statistics world this is apparently not a problem because the researcher can report the results with a wide confidence interval that includes zero, but it is not clear why a granting agency should fund studies that cannot even provide information about the direction of an effect in the population.

Cummings then points out that “one problem is that we never know true power, the probability that our experiment will yield a statistically significant result, because we do not know the true effect size; that is why we are doing the experiment!” (p. 24). The exclamation mark indicates that this is the final dagger in the coffin of power analysis. Power analysis is useless because it makes assumptions about effect sizes when we can just do an experiment to observe the effect size. It is that easy in the world of new statistics. The problem is that we do not know the true effect sizes after an experiment either. We never know the true effect size because we can never determine a population parameter, just like we can never prove the null-hypothesis. It is only possible to estimate population parameter. However, before we estimate a population parameter, we may simply want to know whether an effect exists at all. Power analysis can help in planning studies so that the sample mean shows the same sign as the population mean with a specified error rate.

Determining Sample Sizes in the New Statistics

Although Cumming does not find power analysis useful, he gives some information about sample sizes. Studies should be planned to have a specified level of precision. Cumming gives an example for a between-subject design with n = 50 per cell (N = 100). He chose to present confidence intervals for unstandardized coefficients. In this case, there is no fixed value for the width of the confidence interval because the sampling variance influences the standard error. However, for standardized coefficients like Cohen’s d, sampling variance will produce variation in standardized coefficients, while the standard error is constant. The standard error is simply 2 / sqrt (N), which equals SE = .2 for N = 100. This value needs to be multiplied by 2 to get the confidence interval, and the 95%CI = d +/- .4.   Thus, it is known before the study is conducted that the confidence interval will span 8/10 of a standard deviation and that an observed effect size of d > .4 is needed to exclude 0 from the confidence interval and to state with 95% confidence that the observed effect size would not have occurred if the true effect size were 0 or in the opposite direction.

The problem is that Cumming provides no guidelines about the level of precision that a researcher should achieve. Is 8/10 of a standard deviation precise enough? Should researchers aim for 1/10 of a standard deviation? So when he suggests that funding agencies should focus on precision, it is not clear what criterion should be used to fund research.

One obvious criterion would be to ensure that precision is sufficient to exclude zero so that the results can be used to state that direction of the observed effect is the same as the direction of the effect in the population that a researcher wants to generalize to. However, as soon as effect sizes are used in the planning of the precision of a study, precision planning is equivalent to power analysis. Thus, the main novel aspect of the new statistics is to ignore effect sizes in the planning of studies, but without providing guidelines about desirable levels of precision. Researchers should be aware that N = 100 in a between-subject design gives a confidence interval that spans 8/10 of a standard deviation. Is that precise enough?

Problem of Questionable Research Practices, Publication Bias, and Multiple Testing

A major problem for any statistical method is the assumption that random sampling error is the only source of error. However, the current replication crisis has demonstrated that reported results are also systematically biased. A major challenge for any statistical approach, old or new, is to deal effectively with systematically biased data.

It is impossible to detect bias in a single study. However, when more than one study is available, it becomes possible to examine whether the reported data are consistent with the statistical assumption that each sample is an independent sample and that the results in each sample are a function of the true effect size and random sampling error. In other words, there is no systematic error that biases the results. Numerous statistical methods have been developed to examine whether data are biased or not.

Cumming (2014) does not mention a single method for detecting bias (Funnel Plot, Eggert regression, Test of Excessive Significance, Incredibility-Index, P-Curve, Test of Insufficient Variance, Replicabiity-Index, P-Uniform). He merely mentions a visual inspection of forest plots and suggests that “if for example, a set of studies is distinctly too homogeneous – it shows distinctly less bouncing around than we would expect from sampling variability… we can suspect selection or distortion of some kind” (p. 23). However, he provides no criteria that explain how variability of observed effect sizes should be compared against predicted variability and how the presence of bias influences the interpretation of a meta-analysis. Thus, he concludes that “even so [biases may exist], meta-analysis can give the best estimates justified by research to date, as well as the best guidance for practitioners” (p. 23). Thus, the new statistics would suggest that extrasensory perception is real because a meta-analysis of Bem’s (2011) infamous Journal of Personality and Social Psychology article shows an effect with a tight confidence interval that does not include zero. In contrast, other researchers have demonstrated with old statistical tools and with the help of post-hoc power that Bem’s results are not credible (Francis, 2012; Schimmack, 2012).

Research Integrity

Cumming also advocates research integrity. His first point is that psychological science should “promote research integrity: (a) a public research literature that is complete and trustworthy and (b) ethical practice, including full and accurate reporting of research” (p. 8). However, his own article falls short of this ideal. His article does not provide a complete, balanced, and objective account of the statistical literature. Rather, Cumming (2014) cheery-picks references that support his claims and does not cite references that are inconvenient for his claims. I give one clear example of bias in his literature review.

He cites Ioannidis’s 2005 paper to argue that p-values and NHST is flawed and should be abandoned. However, he does not cite Ioannidis and Trikalinos (2007). This article introduces a statistical approach that can detect biases in meta-analysis by comparing the success rate (percentage of significant results) to the observed power of the studies. As power determines the success rate in an honest set of studies, a higher success rate reveals publication bias. Cumming not only fails to mention this article. He goes on to warn readers “beware of any power statement that does not state an ES; do not use post hoc power.” Without further elaboration, this would imply that readers should ignore evidence for bias with the Test of Excessive Significance because it relies on post-hoc power. To support this claim, he cites Hoenig and Heisey (2001) to claim that “post hoc power can often take almost any value, so it is likely to be misleading” (p. 24). This statement is misleading because post-hoc power is no different from any other statistic that is influenced by sampling error. In fact,Hoenig and Heisey (2001) show that post-hoc power in a single study is monotonically related to p-values. Their main point is that post-hoc power provides no other information than p-values. However, like p-values, post-hoc power becomes more informative, the higher it is. A study with 99% post-hoc power is likely to be a high powered study, just like extremely low p-values, p < .0001, are unlikely to be obtained in low powered studies or in studies when the null-hypothesis is true. So, post-hoc power is informative when it is high. Cumming (2014) further ignores that variability of post-hoc power estimates decreases in a meta-analysis of post-hoc power and that post-hoc power has been used successfully to reveal bias in published articles (Francis, 2012; Schimmack (2012). Thus, his statement that researchers should ignore post-hoc power analyses is not supported by an unbiased review of the literature, and his article does not provide a complete and trustworthy account of the public research literature.


I cannot recommend Cumming’s new statistics. I routinely report confidence intervals in my empirical articles, but I do not consider them as a new statistical tool. In my opinion, the root cause of the credibility crisis is that researchers conduct underpowered studies that have a low chance to produce the predicted effect and then use questionable research practices to boost power and to hide non-significant results that could not be salvaged. A simple solution to this problem is to conduct more powerful studies that can produce significant results when the predict effect exists. I do not claim that this is a new insight. Rather, Jacob Cohen has tried his whole life to educate psychologists about the importance of statistical power.

Here is what Jacob Cohen had to say about the new statistics in 1994 using time-travel to comment on Cumming’s article 20 years later.

“Everyone knows” that confidence intervals contain all the information to be found in significance tests and much more. They not only reveal the status of the trivial nil hypothesis but also about the status of non-nil null hypotheses and thus help remind researchers about the possible operation of the crud factor. Yet they are rarely to be found in the literature. I suspect that the main reason they are not reported is that they are so embarrassingly large! But their sheer size should move us toward improving our measurement by seeking to reduce the unreliable and invalid part of the variance in our measures (as Student himself recommended almost a century ago). Also, their width provides us with the analogue of power analysis in significance testing—larger sample sizes reduce the size of confidence intervals as they increase the statistical power of NHST” (p. 1002).

If you are looking for a book on statistics, I recommend Cohen’s old statistics over Cumming’s new statistics, p < .05.

Conflict of Interest: I do not have a book to sell (yet), but I strongly believe that power analysis is an important tool for all scientists who have to deal with uncontrollable variance in their data. Therefore I am strongly opposed to Cumming’s push for a new statistics that provides no guidelines for researchers how they can optimize the use of their resources to obtain credible evidence for effects that actually exist and no guidelines how science can correct false positive results.


Bayesian Statistics in Small Samples: Replacing Prejudice against the Null-Hypothesis with Prejudice in Favor of the Null-Hypothesis

Matzke, Nieuwenhuis, van Rijn, Slagter, van der Molen, and Wagenmakers (2015) published the results of a preregistered adversarial collaboration. This article has been considered a model of conflict resolution among scientists.

The study examined the effect of eye-movements on memory. Drs. Nieuwenhuis and Slagter assume that horizontal eye-movements improve memory. Drs. Matzke, van Rijn, and Wagenmakers did not believe that horizontal-eye movements improve memory. That is, they assumed the null-hypothesis to be true. Van der Molen acted as a referee to resolve conflict about procedural questions (e.g., should some participants be excluded from analysis?).

The study was a between-subject design with three conditions: horizontal eye movements, vertical eye movements, and no eye movement.

The researchers collected data from 81 participants and agreed to exclude 2 participants, leaving 79 participants for analysis. As a result there were 27 or 26 participants per condition.

The hypothesis that horizontal eye-movements improve performance can be tested in several ways.

An overall F-test can compare the means of the three groups against the hypothesis that they are all equal. This test has low power because nobody predicted differences between vertical eye-movements and no eye-movements.

A second alternative is to compare the horizontal condition against the combined alternative groups. This can be done with a simple t-test. Given the directed hypothesis, a one-tailed test can be used.

Power analysis with the free software program GPower shows that this design has 21% power to reject the null-hypothesis with a small effect size (d = .2). Power for a moderate effect size (d = .5) is 68% and power for a large effect size (d = .8) is 95%.

Thus, the decisive study that was designed to solve the dispute only has adequate power (95%) to test Drs. Matzke et al.’s hypothesis d = 0 against the alternative hypothesis that d = .8. For all effect sizes between 0 and .8, the study was biased in favor of the null-hypothesis.

What does an effect size of d = .8 mean? It means that memory performance is boosted by .8 standard deviations. For example, if students take a multiple-choice exam with an average of 66% correct answers and a standard deviation of 15%, they could boost their performance by 12% points (15 * 0.8 = 12) from an average of 66% (C) to 78% (B+) by moving their eyes horizontally while thinking about a question.

The article makes no mention of power-analysis and the implicit assumption that the effect size has to be large to avoid biasing the experiment in favor of the critiques.

Instead the authors used Bayesian statistics; a type of statistics that most empirical psychologists understand even less than standard statistics. Bayesian statistics somehow magically appears to be able to draw inferences from small samples. The problem is that Bayesian statistics requires researchers to specify a clear alternative to the null-hypothesis. If the alternative is d = .8, small samples can be sufficient to decide whether an observed effect size is more consistent with d = 0 or d = .8. However, with more realistic assumptions about effect sizes, small samples are unable to reveal whether an observed effect size is more consistent with the null-hypothesis or a small to moderate effect.

Actual Results

So what where the actual results?

Condition                                          Mean     SD         

Horizontal Eye-Movements          10.88     4.32

Vertical Eye-Movements               12.96     5.89

No Eye Movements                       15.29     6.38      

The results provide no evidence for a benefit of horizontal eye movements. In a comparison of the two a priori theories (d = 0 vs. d > 0), the Bayes-Factor strongly favored the null-hypothesis. However, this does not mean that Bayesian statistics has magical powers. The reason was that the empirical data actually showed a strong effect in the opposite direction, in that participants in the no-eye-movement condition had better performance than in the horizontal-eye-movement condition (d = -.81).   A Bayes Factor for a two-tailed hypothesis or the reverse hypothesis would not have favored the null-hypothesis.


In conclusion, a small study surprisingly showed a mean difference in the opposite prediction than previous studies had shown. This finding is noteworthy and shows that the effects of eye-movements on memory retrieval are poorly understood. As such, the results of this study are simply one more example of the replicability crisis in psychology.

However, it is unfortunate that this study is published as a model of conflict resolution, especially as the empirical results failed to resolve the conflict. A key aspect of a decisive study is to plan a study with adequate power to detect an effect.   As such, it is essential that proponents of a theory clearly specify the effect size of their predicted effect and that the decisive experiment matches type-I and type-II error. With the common 5% Type-I error this means that a decisive experiment must have 95% power (1 – type II error). Bayesian statistics does not provide a magical solution to the problem of too much sampling error in small samples.

Bayesian statisticians may ignore power analysis because it was developed in the context of null-hypothesis testing. However, Bayesian inferences are also influenced by sample size and studies with small samples will often produce inconclusive results. Thus, it is more important that psychologists change the way they collect data than to change the way they analyze their data. It is time to allocate more resources to fewer studies with less sampling error than to waste resources on many studies with large sampling error; or as Cohen said: Less is more.