It was relatively quiet on academic twitter when most academics were enjoying the last weeks of summer before the start of a new, new-normal semester. This changed on August 17, when the datacolada crew published a new blog post that revealed fraud in a study of dishonesty (http://datacolada.org/98). Suddenly, the integrity of social psychology was once again discussed on twitter, in several newspaper articles, and an article in Science magazine (O’Grady, 2021). The discovery of fraud in one dataset raises questions about other studies in articles published by the same researcher as well as in social psychology in general (“some researchers are calling Ariely’s large body of work into question”; O’Grady, 2021).
The brouhaha about the discovery of fraud is understandable because fraud is widely considered an unethical behavior that violates standards of academic integrity that may end a career (e.g., Stapel). However, there are many other reasons to be suspect of the credibility of Dan Ariely’s published results and those by many other social psychologists. Over the past decade, strong scientific evidence has accumulated that social psychologists’ research practices were inadequate and often failed to produce solid empirical findings that can inform theories of human behavior, including dishonest ones.
Arguably, the most damaging finding for social psychology was the finding that only 25% of published results could be replicated in a direct attempt to reproduce original findings (Open Science Collaboration, 2015). With such a low base-rate of successful replications, all published results in social psychology journals are likely to fail to replicate. The rational response to this discovery is to not trust anything that is published in social psychology journals unless there is evidence that a finding is replicable. Based on this logic, the discovery of fraud in a study published in 2012 is of little significance. Even without fraud, many findings are questionable.
Questionable Research Practices
The idealistic model of a scientist assumes that scientists test predictions by collecting data and then let the data decide whether the prediction was true or false. Articles are written to follow this script with an introduction that makes predictions, a results section that tests these predictions, and a conclusion that takes the results into account. This format makes articles look like they follow the ideal model of science, but it only covers up the fact that actual science is produced in a very different way; at least in social psychology before 2012. Either predictions are made after the results are known (Kerr, 1998) or the results are selected to fit the predictions (Simmons, Nelson, & Simonsohn, 2011).
This explains why most articles in social psychology support authors’ predictions (Sterling, 1959; Sterling et al., 1995; Motyl et al., 2017). This high success rate is not the result of brilliant scientists and deep insights into human behaviors. Instead, it is explained by selection for (statistical) significance. That is, when a result produces a statistically significant result that can be used to claim support for a prediction, researchers write a manuscript and submit it for publication. However, when the result is not significant, they do not write a manuscript. In addition, researchers will analyze their data in multiple ways. If they find one way that supports their predictions, they will report this analysis, and not mention that other ways failed to show the effect. Selection for significance has many names such as publication bias, questionable research practices, or p-hacking. Excessive use of these practices makes it easy to provide evidence for false predictions (Simmons, Nelson, & Simonsohn, 2011). Thus, the end-result of using questionable practices and fraud can be the same; published results are falsely used to support claims as scientifically proven or validated, when they actually have not been subjected to a real empirical test.
Although questionable practices and fraud have the same effect, scientists make a hard distinction between fraud and QRPs. While fraud is generally considered to be dishonest and punished with retractions of articles or even job losses, QRPs are tolerated. This leads to the false impression that articles that have not been retracted provide credible evidence and can be used to make scientific arguments (studies show ….). However, QRPs are much more prevalent than outright fraud and account for the majority of replication failures, but do not result in retractions (John, Loewenstein, & Prelec, 2012; Schimmack, 2021).
The good news is that the use of QRPs is detectable even when original data are not available, whereas fraud typically requires access to the original data to reveal unusual patterns. Over the past decade, my collaborators and I have worked on developing statistical tools that can reveal selection for significance (Bartos & Schimmack, 2021; Brunner & Schimmack, 2020; Schimmack, 2012). I used the most advanced version of these methods, z-curve.2.0, to examine the credibility of results published in Dan Ariely’s articles.
Data
To examine the credibility of results published in Dan Ariely’s articles I followed the same approach that I used for other social psychologists (Replicability Audits). I selected articles based on authors’ H-Index in WebOfKnowledge. At the time of coding, Dan Ariely had an H-Index of 47; that is, he published 47 articles that were cited at least 47 times. I also included the 48th article that was cited 47 times. I focus on the highly cited articles because dishonest reporting of results is more harmful, if the work is highly cited. Just like a falling tree may not make a sound if nobody is around, untrustworthy results in an article that is not cited have no real effect.
For all empirical articles, I picked the most important statistical test per study. The coding of focal results is important because authors may publish non-significant results when they made no prediction. They may also publish a non-significant result when they predict no effect. However, most claims are based on demonstrating a statistically significant result. The focus on a single result is needed to ensure statistical independence which is an assumption made by the statistical model. When multiple focal tests are available, I pick the first one unless another one is theoretically more important (e.g., featured in the abstract). Although this coding is subjective, other researchers including Dan Ariely can do their own coding and verify my results.
Thirty-one of the 48 articles reported at least one empirical study. As some articles reported more than one study, the total number of studies was k = 97. Most of the results were reported with test-statistics like t, F, or chi-square values. These values were first converted into two-sided p-values and then into absolute z-scores. 92 of these z-scores were statistically significant and used for a z-curve analysis.
Z-Curve Results
The key results of the z-curve analysis are captured in Figure 1.
Figure 1
Visual inspection of the z-curve plot shows clear evidence of selection for significance. While a large number of z-scores are just statistically significant (z > 1.96 equals p < .05), there are very few z-scores that are just shy of significance (z < 1.96). Moreover, the few z-scores that do not meet the standard of significance were all interpreted as sufficient evidence for a prediction. Thus, Dan Ariely’s observed success rate is 100% or 95% if only p-values below .05 are counted. As pointed out in the introduction, this is not a unique feature of Dan Ariely’s articles, but a general finding in social psychology.
A formal test of selection for significance compares the observed discovery rate (95% z-scores greater than 1.96) to the expected discovery rate that is predicted by the statistical model. The prediction of the z-curve model is illustrated by the blue curve. Based on the distribution of significant z-scores, the model expected a lot more non-significant results. The estimated expected discovery rate is only 15%. Even though this is just an estimate, the 95% confidence interval around this estimate ranges from 5% to only 31%. Thus, the observed discovery rate is clearly much much higher than one could expect. In short, we have strong evidence that Dan Ariely and his co-authors used questionable practices to report more successes than their actual studies produced.
Although these results cast a shadow over Dan Ariely’s articles, there is a silver lining. It is unlikely that the large pile of just significant results was obtained by outright fraud; not impossible, but unlikely. The reason is that QRPs are bound to produce just significant results, but fraud can produce extremely high z-scores. The fraudulent study that was flagged by datacolada has a z-score of 11, which is virtually impossible to produce with QRPs (Simmons et al., 2001). Thus, while we can disregard many of the results in Ariely’s articles, he does not have to fear to lose his job (unless more fraud is uncovered by data detectives). Ariely is also in good company. The expected discovery rate for John A. Bargh is 15% (Bargh Audit) and the one for Roy F. Baumester is 11% (Baumeister Audit).
The z-curve plot also shows some z-scores greater than 3 or even greater than 4. These z-scores are more likely to reveal true findings (unless they were obtained with fraud) because (a) it gets harder to produce high z-scores with QRPs and replication studies show higher success rates for original studies with strong evidence (Schimmack, 2021). The problem is to find a reasonable criterion to distinguish between questionable results and credible results.
Z-curve make it possible to do so because the EDR estimates can be used to estimate the false discovery risk (Schimmack & Bartos, 2021). As shown in Figure 1, with an EDR of 15% and a significance criterion of alpha = .05, the false discovery risk is 30%. That is, up to 30% of results with p-values below .05 could be false positive results. The false discovery risk can be reduced by lowering alpha. Figure 2 shows the results for alpha = .01. The estimated false discovery risk is now below 5%. This large reduction in the FDR was achieved by treating the pile of just significant results as no longer significant (i.e., it is now on the left side of the vertical red line that reflects significance with alpha = .01, z = 2.58).
With the new significance criterion only 51 of the 97 tests are significant (53%). Thus, it is not necessary to throw away all of Ariely’s published results. About half of his published results might have produced some real evidence. Of course, this assumes that z-scores greater than 2.58 are based on real data. Any investigation should therefore focus on results with p-values below .01.
The final information that is provided by a z-curve analysis is the probability that a replication study with the same sample size produces a statistically significant result. This probability is called the expected replication rate (ERR). Figure 1 shows an ERR of 52% with alpha = 5%, but it includes all of the just significant results. Figure 2 excludes these studies, but uses alpha = 1%. Figure 3 estimates the ERR only for studies that had a p-value below .01 but using alpha = .05 to evaluate the outcome of a replication study.
Figur e3
In Figure 3 only z-scores greater than 2.58 (p = .01; on the right side of the dotted blue line) are used to fit the model using alpha = .05 (the red vertical line at 1.96) as criterion for significance. The estimated replication rate is 85%. Thus, we would predict mostly successful replication outcomes with alpha = .05, if these original studies were replicated and if the original studies were based on real data.
Conclusion
The discovery of a fraudulent dataset in a study on dishonesty has raised new questions about the credibility of social psychology. Meanwhile, the much bigger problem of selection for significance is neglected. Rather than treating studies as credible unless they are retracted, it is time to distrust studies unless there is evidence to trust them. Z-curve provides one way to assure readers that findings can be trusted by keeping the false discovery risk at a reasonably low level, say below 5%. Applying this methods to Ariely’s most cited articles showed that nearly half of Ariely’s published results can be discarded because they entail a high false positive risk. This is also true for many other findings in social psychology, but social psychologists try to pretend that the use of questionable practices was harmless and can be ignored. Instead, undergraduate students, readers of popular psychology books, and policy makers may be better off by ignoring social psychology until social psychologists report all of their results honestly and subject their theories to real empirical tests that may fail. That is, if social psychology wants to be a science, social psychologists have to act like scientists.
After trying several traditional journals that are falsely considered to be prestigious because they have high impact factors, we are proud to announce that our manuscript “Z-curve 2.0: : Estimating Replication Rates and Discovery Rates” has been accepted for publication in Meta-Psychology. We received the most critical and constructive comments of our manuscript during the review process at Meta-Psychology and are grateful for many helpful suggestions that improved the clarity of the final version. Moreover, the entire review process is open and transparent and can be followed when the article is published. Moreover, the article is freely available to anybody interested in Z-Curve.2.0, including users of the zcurve package (https://cran.r-project.org/web/packages/zcurve/index.html).
Although the article will be freely available on the Meta-Psychology website, the latest version of the manuscript is posted here is a blog post. Supplementary materials can be found on OSF (https://osf.io/r6ewt/)
Z-curve 2.0: Estimating Replication and Discovery Rates
František Bartoš1,2,*, Ulrich Schimmack3 1 University of Amsterdam 2 Faculty of Arts, Charles University 3 University of Toronto, Mississauga
Correspondence concerning this article should be addressed to: František Bartoš, University of Amsterdam, Department of Psychological Methods, Nieuwe Achtergracht 129-B, 1018 VZ Amsterdam, The Netherlands, fbartos96@gmail.com
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Abstract
Selection for statistical significance is a well-known factor that distorts the published literature and challenges the cumulative progress in science. Recent replication failures have fueled concerns that many published results are false-positives. Brunner and Schimmack (2020) developed z-curve, a method for estimating the expected replication rate (ERR) – the predicted success rate of exact replication studies based on the mean power after selection for significance. This article introduces an extension of this method, z-curve 2.0. The main extension is an estimate of the expected discovery rate (EDR) – the estimate of a proportion that the reported statistically significant results constitute from all conducted statistical tests. This information can be used to detect and quantify the amount of selection bias by comparing the EDR to the observed discovery rate (ODR; observed proportion of statistically significant results). In addition, we examined the performance of bootstrapped confidence intervals in simulation studies. Based on these results, we created robust confidence intervals with good coverage across a wide range of scenarios to provide information about the uncertainty in EDR and ERR estimates. We implemented the method in the zcurve R package (Bartoš & Schimmack, 2020).
It has been known for decades that the published record in scientific journals is not representative of all studies that are conducted. For a number of reasons, most published studies are selected because they reported a theoretically interesting result that is statistically significant; p < .05 (Rosenthal & Gaito, 1964; Scheel, Schijen, & Lakens, 2021; Sterling, 1959; Sterling et al., 1995). This selective publishing of statistically significant results introduces a bias in the published literature. At the very least, published effect sizes are inflated. In the most extreme cases, a false-positive result is supported by a large number of statistically significant results (Rosenthal, 1979).
Some sciences (e.g., experimental psychology) tried to reduce the risk of false-positive results by demanding replication studies in multiple-study articles (cf. Wegner, 1992). However, internal replication studies provided a false sense of replicability because researchers used questionable research practices to produce successful internal replications (Francis, 2014; John, Lowenstein, & Prelec, 2012; Schimmack, 2012). The pervasive presence of publication bias at least partially explains replication failures in social psychology (Open Science Collaboration, 2015; Pashler & Wagenmakers, 2012, Schimmack, 2020); medicine (Begley & Ellis, 2012; Prinz, Schlange, & Asadullah 2011), and economics (Camerer et al., 2016; Chang & Li, 2015).
In meta-analyses, the problem of publication bias is usually addressed by one of the different methods for its detection and a subsequent adjustment of effect size estimates. However, many of them (Egger, Smith, Schneider, & Minder, 1997; Ioannidis and Trikalinos, 2007; Schimmack, 2012) perform poorly under conditions of heterogeneity (Renkewitz & Keiner, 2019), whereas others employ a meta-analytic model assuming that the studies are conducted on a single phenomenon (e.g., Hedges, 1992; Vevea & Hedges, 1995; Maier, Bartoš & Wagenmakers, in press). Moreover, while the aforementioned methods test for publication bias (return a p-value or a Bayes factor), they usually do not provide a quantitative estimate of selection bias. An exception would be the publication probabilities/ratios estimates from selection models (e.g., Hedges, 1992). Maximum likelihood selection models work well when the distribution of effect sizes is consistent with model assumptions, but can be biased when the distribution when the actual distribution does not match the expected distribution (e.g., Brunner & Schimmack, 2020; Hedges, 1992; Vevea & Hedges, 1995). Brunner and Schimmack (2020) introduced a new method that does not require a priori assumption about the distribution of effect sizes. The z-curve method uses a finite mixture model to correct for selection bias. We extended z-curve to also provide information about the amount of selection bias. To distinguish between the new and old z-curve methods, we refer to the old z-curve as z-curve 1.0 and the new z-curve as z-curve 2.0. Z-curve 2.0 has been implemented in the open statistic program R as the zcurve package that can be downloaded from CRAN (Bartoš & Schimmack, 2020).
Before we introduce z-curve 2.0, we would like to introduce some key statistical terms. We assume that readers are familiar with the basic concepts of statistical significance testing; normal distribution, null-hypothesis, alpha, type-I error, and false-positive result (see Bartoš & Maier, in press, for discussion of some of those concepts and their relation).
Glossary
Power is defined as the long-run relative frequency of statistically significant results in a series of exact replication studies with the same sample size when the null-hypothesis is false. For example, in a study with two groups (n = 50), a population effect size of Cohen’s d = 0.4 has 50.8% power to produce a statistically significant result. Thus, 100 replications of this study are expected to produce approximately 50 statistically significant results. The actual frequency will approach 50.8% as the study is repeated infinitely.
Unconditional power extends the concept of power to studies where the null-hypothesis is true. Typically, power is a conditional probability assuming a non-zero effect size (i.e., the null-hypothesis is false). However, the long-run relative frequency of statistically significant results is also known when the null-hypothesis is true. In this case, the long-run relative frequency is determined by the significance criterion, alpha. With alpha = 5%, we expect that 5 out of 100 studies will produce a statistically significant result. We use the term unconditional power to refer to the long-run frequency of statistically significant results without conditioning on a true effect. When the effect size is zero and alpha is 5%, unconditional power is 5%. As we only consider unconditional power in this article, we will use the term power to refer to unconditional power, just like Canadians use the term hockey to refer to ice hockey.
Mean (unconditional) power is a summary statistic of studies that vary in power. Mean power is simply the arithmetic mean of the power of individual studies. For example, two studies with power = .4 and power = .6, have a mean power of .5.
Discovery rate is a relative frequency of statistically significant results. Following Soric (1989), we call statistically significant results discoveries. For example, if 100 studies produce 36 statistically significant results, the discovery rate is 36%. Importantly, the discovery rate does not distinguish between true or false discoveries. If only false-positive results were reported, the discovery rate would be 100%, but none of the discoveries would reflect a true effect (Rosenthal, 1979).
Selection bias is a process that favors the publication of statistically significant results. Consequently, the published literature has a higher percentage of statistically significant results than was among the actually conducted studies. It results from significance testing that creates two classes of studies separated by the significance criterion alpha. Those with a statistically significant result, p < .05, where the null-hypothesis is rejected, and those with a statistically non-significant result, where the null-hypothesis is not rejected, p > .05. Selection for statistical significance limits the population of all studies that were conducted to the population of studies with statistically significant results. For example, if two studies produce p-values of .20 and .01, only the study with the p-value .01 is retained. Selection bias is often called publication bias. Studies show that authors are more likely to submit findings for publication when the results are statistically significant (Franco, Malhotra & Simonovits, 2014).
Observed discovery rate (ODR) is the percentage of statistically significant results in an observed set of studies. For example, if 100 published studies have 80 statistically significant results, the observed discovery rate is 80%. The observed discovery rate is higher than the true discovery rate when selection bias is present.
Expected discovery rate (EDR) is the mean power before selection for significance; in other words, the mean power of all conducted studies with statistically significant and non-significant results. As power is the long-run relative frequency of statistically significant results, the mean power before selection for significance is the expected relative frequency of statistically significant results. As we call statistically significant results discoveries, we refer to the expected percentage of statistically significant results as the expected discovery rate. For example, if we have two studies with power of .05 and .95, we are expecting 1 statistically significant result and an EDR of 50%, (.95 + .05)/2 = .5.
Expected replication rate (ERR) is the mean power after selection for significance, in other words, the mean power of only the statistically significant studies. Furthermore, since most people would declare a replication successful only if it produces a result in the same direction, we base ERR on the power to obtain a statistically significant result in the same direction. Using the prior example, we assume that the study with 5% power produced a statistically non-significant result and the study with 95% power produced a statistically significant result. In this case, we end up with only one statistically significant result with 95% power. Subsequently, the mean power after selection for significance is 95% (there is almost zero chance that a study with 95% power would produce replication with an outcome in the opposite direction). Based on this estimate, we would predict that 95% of exact replications of this study with the same sample size, and therefore with 95% power, will be statistically significant in the same direction.
As mean power after selection for significance predicts the relative frequency of statistically significant results in replication studies, we call it the expected replication rate. The ERR also corresponds to the “aggregate replication probability” discussed by Miller (2009).
Numerical Example
Before introducing the formal model, we illustrate the concepts with a fictional example. In the example, researchers test 100 true hypotheses with 100% power (i.e., every test of a true hypothesis produces p < .05) and 100 false hypotheses (H0 is true) with 5% power which is determined by alpha = .05. Consequently, the researchers obtain 100 true positive results and 5 false-positive results, for a total of 105 statistically significant results.[1] The expected discovery rate is (1 × 100 + 0.05 × 100)/(100 + 100) = 105/200 = 52.5% which corresponds to the observed discovery rate when all conducted studies are reported.
So far, we have assumed that there is no selection bias. However, let us now assume that 50 of the 95 statistically non-significant results are not reported. In this case, the observed discovery rate increased from 105/200 to 105/150 = 70%. The discrepancy between the EDR, 52.5%, and the ODR, 70%, provides quantitative information about the amount of selection bias.
As shown, the EDR provides valuable information about the typical power of studies and about the presence of selection bias. However, it does not provide information about the replicability of the statistically significant results. The reason is that studies with higher power are more likely to produce a statistically significant result in replications (Brunner & Schimmack, 2020; Miller, 2009). The main purpose of z-curve 1.0 was to estimate the mean power after selection for significance to predict the outcome of exact replication studies. In the example, only 5 of the 100 false hypotheses were statistically significant. In contrast, all 100 tests of the true hypothesis were statistically significant. This means that the mean power after selection for significance is (5 × .025 + 100 × 1)/(5 + 100) = 100.125/105 ≈ 95.4%, which is the expected replication rate.
Formal Introduction
Unfortunately, there is no standard symbol for power, which is usually denoted as 1 – β, with β being the probability of a type-II error. We propose to use epsilon, ε, as a Greek symbol for power because one Greek word for power starts with this letter (εξουσία). We further add subscript 1 or 2, depending on whether the direction of the outcome is relevant or not. Therefore, denotes power of a study regardless of the direction of the outcome and denotes power of a study in a specified direction.
The EDR,
is defined as the mean power (ε2) of a set of K studies, independent on the outcome direction.
Following Brunner and Schimmack (2020), the expected replication rate (ERR) is defined as the ratio of mean squared power and mean power of all studies, statistically significant and non-significant ones. We modify the definition here by taking the direction of the replication study into account.[2] The mean square power in the nominator is used because we are computing the expected relative frequency of statistically significant studies produced by a set of already statistically significant studies – if a study produces a statistically significant result with probability equal to its power, the chance that the same study will again be significant is power squared. The mean power in the denominator is used because we are restricting our selection to only already statistically significant studies which are produced at the rate corresponding to their power (see also Miller, 2009). The ratio simplifies by omitting division by K in both the nominator and denominator to:
which can also be read as a weighted mean power, where each power is weighted by itself. The weights originate from the fact that studies with higher power are more likely to produce statistically significant results. The weighted mean power of all studies is therefore equal to the unweighted mean power of the studies selected for significance (ksig; cf. Brunner & Schimmack, 2020).
If we have a set of studies with the same power (e.g., set of exact replications with the same sample size) that test for an effect with a z-test, the p-values converted to z-statistics follow a normal distribution with mean and a standard deviation equal to 1. Using an alpha level α, the power is the tail area of a standard normal distribution (Φ) centered over a mean, (μz) on the left and right side of the z-scores corresponding to alpha, -1.96 and 1.96 (with the usual alpha = .05),
or the tail area on the right side of the z-score corresponding to alpha, when we are also considering whether the directionality of the effect,
Two-sided p-values do not preserve the direction of the deviation from null and we cannot know whether a z-statistic comes from the lower or upper tail of the distribution. Therefore, we work with absolute values of z-statistics, changing their distribution from normal to folded normal distribution (Elandt, 1961; Leone, Nelson, & Nottingham, 1961).
Figure 1 illustrates the key concepts of z-curve with various examples. The first three density plots in the first row show the sampling distributions for studies with low (ε = 0.3), medium (ε = 0.5), and high (ε = .8) power, respectively. The last density plots illustrate the distribution that is obtained for a mixture of studies with low, medium, and high power with equal frequency (33.3% each). It is noteworthy that all four density distributions have different shapes. While Figure 1 illustrates how differences in power produce differences in the shape of the distributions, z-curve works backward and uses the shape of the distribution to estimate power.
Figure 1. Density (y-axis) of z-statistics (x-axis) generated by studies with different powers (columns) across different stages of the publication process (rows). The first row shows a distribution of z-statistics from z-tests homogeneous in power (the first three columns) or by their mixture (the fourth column). The second row shows only statistically significant z-statistics. The third row visualizes EDR as a proportion of statistically significant z-statistics out of all z-statistics. The fourth row shows a distribution of z-statistics from exact replications of only the statistically significant studies (dashed line for non-significant replication studies). The fifth row visualizes ERR as a proportion of statistically significant exact replications out of statistically significant studies.
Although z-curve can be used to fit the distributions in the first row, we assume that the observed distribution of all z-statistics is distorted by the selection bias. Even if some statistically non-significant p-values are reported, their distribution is subject to unknown selection effects. Therefore, by default z-curve assumes that selection bias is present and uses only the distribution of statistically significant results. This changes the distributions of z-statistics to folded normal distributions that are truncated at the z-score corresponding to the significance criterion, which is typically z = 1.96 for p = .05 (two-tailed). The second row in Figure 1 shows these truncated folded normal distributions. Importantly, studies with different levels of power produce different distributions despite the truncation. The different shapes of truncated distributions make it possible to estimate power by fitting a model to the truncated distribution. The third row of Figure 1 illustrates the EDR as a proportion of statistically significant studies from all conducted studies. We use Equation 3 to re-express EDR (Equation 2), which equals the mean unconditional power, of a set of K heterogenous studies using the means of sampling distributions of their z-statistics, μz,k,
Z-curve makes it possible to estimate the shape of the distribution in the region of statistically non-significant results on the basis of the observed distribution of statistically significant results. That is, after fitting a model to the grey area of the curve, it extrapolates the full distribution.
The fourth row of Figure 1 visualizes a distribution of expected z-statistics if the statistically significant studies were to be exactly replicated (not depicting the small proportion of results in the opposite direction than the original, significant, result). The full line highlights the portion of studies that would produce a statistically significant result, with the distribution of statistically non-significant studies drawn using the dashed line. An exact replication with the same sample size of the studies in the grey area in the second row is not expected to reproduce the truncated distribution again because truncation is a selection process. The replication distribution is not truncated and produces statistically significant and non-significant results. By modeling the selection process, z-curve predicts the non-truncated distributions in the fourth row from the truncated distributions in the second row.
The fifth row of Figure 1 visualizes ERR as a proportion of statistically significant exact replications in the expected direction from a set of the previously statistically significant studies. The ERR (Equation 1) of a set ofheterogeneous studies can be again re-expressed using Equations 3 and 4 with the means of sampling distributions of their z-statistics,
Z-curve 2.0
Z-curve is a finite mixture model (Brunner & Schimmack, 2020). Finite mixture models leverage the fact that an observed distribution of statistically significant z-statistics is a mixture of K truncated folded normal distribution with means and standard deviations 1. Instead of trying to estimate of every single observed z-statistic, a finite mixture model approximates the observed distribution based on K studies with a smaller set of J truncated folded normal distributions, , with J < K components,
Each mixture component j approximates a proportion of observed z-statistics with a probability density function, , of truncated folded normal distribution with parameters – a mean and standard deviation equal to 1. For example, while actual studies may vary in power from 40% to 60%, a mixture model may represent all of these studies with a single component with 50% power.
Z-curve 1.0 used three components with varying means. Extensive testing showed that varying means produced poor estimates of the EDR. Therefore, we switched to models with fixed means and increased the number of components to seven. The seven components are equally spaced by one standard deviation from z = 0 (power = alpha) to 6 (power ~ 1). As power for z-scores greater than 6 is essentially 1, it is not necessary to model the distribution of z-scores greater than 6, and all z-scores greater than 6 are assigned a power value of 1 (Brunner & Schimmack, 2020). The power values implied by the 7 components are .05, .17, .50, .85, .98, .999, .99997. We also tried a model with equal spacing of power, and we tried models with fewer or more components, but neither did improve performance in simulation studies.
We use the model parameter estimates to compute the estimated the EDR and ERR as the weighted average of seven truncated folded normal distributions centered over z = 0 to 6,
Curve Fitting
Z-curve 1.0 used an unorthodox approach to find the best fitting model that required fitting a truncated kernel-density distribution to the statistically significant z-statistics (Brunner & Schimmack, 2020). This is a non-trivial step that may produce some systematic bias in estimates. Z-curve 2.0 makes it possible to fit the model directly to the observed z-statistics using the well-established expectation maximization (EM) algorithm that is commonly used to fit mixture models (Dempster, Laird, & Rubin, 1977, Lee & Scott, 2012). Using the EM algorithm has the advantage that it is a well-validated method to fit mixture models. It is beyond the scope of this article to explain the mechanics of the EM algorithm (cf. Bishop, 2006), but it is important to point out some of its potential limitations. The main limitation is that it may terminate the search for the best fit before the best fitting model has been found. In order to prevent this, we run 20 searches with randomly selected starting values and terminate the algorithm in the first 100 iterations, or if the criterion falls below 1e-3. We then select the outcome with the highest likelihood value and continue until 1000 iterations or a criterion value of 1e-5 is reached. To speed up the fitting process, we optimized the procedure using Rcpp (Eddelbuettel et al., 2011).
Information about point estimates should be accompanied by information about uncertainty whenever possible. The most common way to do so is by providing confidence intervals. We followed the common practice of using bootstrapping to obtain confidence intervals for mixture models (Ujeh et al., 2016). As bootstrapping is a resource-intensive process, we used 500 samples for the simulation studies. Users of the z-curve package can use more iterations to analyze actual data.
Simulations
Brunner and Schimmack (2020) compared several methods for estimating mean power and found that z-curve performed better than three competing methods. However, these simulations were limited to the estimation of the ERR. Here we present new simulation studies to examine the performance of z-curve as a method to estimate the EDR as well. One simulation directly simulated power distributions, the other one simulated t-tests. We report the detailed results of both simulation studies in a Supplement. For the sake of brevity, we focus on the simulation of t-tests because readers can more easily evaluate the realism of these simulations. Moreover, most tests in psychology are t-tests or F-tests and Bruner and Schimmack (2020) already showed that the numerator degrees of freedom of F-tests do not influence results. Thus, the results for t-tests can be generalized to F-tests and z-tests.
The simulation was a complex 4 x 4 x 4 x 3 x 3 design with 576 cells. The first factor of the design that was manipulated was the mean effect size with Cohen’s ds ranging from 0 to 0.6 (0, 0.2, 0.4., 0.6). The second factor in the design was heterogeneity in effect sizes was simulated with a normal distribution around the mean effect size with SDs ranging from 0 to 0.6 (0, 0.2, 0.4., 0.6). Preliminary analysis with skewed distributions showed no influence of skew. The third factor of the design was sample size for between-subject design with N = 50, 100, and 200. The fourth factor of the design was the percentage of true null-hypotheses that ranged from 0 to 60% (0%, 20%, 40%, 60%). The last factor of the design was the number of studies with sets of k = 100, 300, and 1,000 statistically significant studies.
Each cell of the design was run 100 times for a total of 57,600 simulations. For the main effects of this design there were 57,600 / 4 = 14,400 or 57,600 / 3 = 19,200 simulations. Even for two-way interaction effects, the number of simulations is sufficient, 57,600 / 16 = 3,600. For higher interactions the design may be underpowered to detect smaller effects. Thus, our simulation study meets recommendations for sample sizes in simulation studies for main effects and two-way interactions, but not for more complex interaction effects (Morris, White, & Crowther, 2019). The code for the simulations is accessible at https://osf.io/r6ewt/.
Evaluation
For a comprehensive evaluation of z-curve 2.0 estimates, we report bias (i.e., mean distance between estimated and true values), root mean square error (RMSE; quantifying the error variance of the estimator), and confidence interval coverage (Morris et al. 2019).[3] To check the performance of the z-curve across different simulation settings, we analyzed the results of the factorial design using analyses of variance (ANOVAs) for continuous measures and logistic regression for the evaluation of confidence intervals (0 = true value not in the interval, 1 = true value in the interval). The analysis scripts and results are accessible at https://osf.io/r6ewt/.
Results
We start with the ERR because it is essentially a conceptual replication study of Brunner and Schimmack’s (2020) simulation studies with z-curve 1.0.
ERR
Visual inspection of the z-curves ERR estimates plotted against the true ERR values did not show any pathological behavior due to the approximation by a finite mixture model (Figure 3).
Figure 3. Estimated (y-axis) vs. true (x-axis) ERR in simulation U across a different number of studies.
Figure 3 shows that even with k = 100 studies, z-curve estimates are clustered close enough to the true values to provide useful predictions about the replicability of sets of studies. Overall bias was less than one percentage point, -0.88 (SEMCMC = 0.04). This confirms that z-curve has high large-sample accuracy (Brunner & Schimmack, 2020). RMSE decreased from 5.14 (SEMCMC = 0.03) percentage points with k = 100 to 2.21 (SEMCMC = 0.01) percentage points with k = 1,000. Thus, even with relatively small sample sizes of 100 studies, z-curve can provide useful information about the ERR.
The Analysis of Variance (ANOVA) showed no statistically significant 5-way interaction or 4-way interactions. A strong three-way interaction was found for effect size, heterogeneity of effect sizes, and sample size, z = 9.42. Despite the high statistical significance, effect sizes were small. Out of the 36 cells of the 4 x 3 x 3 design, 32 cells showed less than one percentage point bias. Larger biases were found when effect sizes were large, heterogeneity was low, and sample sizes were small. The largest bias was found for Cohen’s d = 0.6, SD = 0, and N = 50. In this condition, ERR was 4.41 (SEMCMC = 0.11) percentage points lower than the true replication rate. The finding that z-curve performs worse with low heterogeneity replicates findings by Brunner and Schimmack (2002). One reason could be that a model with seven components can easily be biased when most parameters are zero. The fixed components may also create a problem when true power is between two fixed levels. Although a bias of 4 percentage points is not ideal, it also does not undermine the value of a model that has very little bias across a wide range of scenarios.
The number of studies had a two-way interaction with effect size, z = 3.8, but bias in the 12 cells of the 4 x 3 design was always less than 2 percentage points. Overall, these results confirm the fairly good large sample accuracy of the ERR estimates.
We used logistic regression to examine patterns in the coverage of the 95% confidence intervals. This time a statistically significant four-way interaction emerged for effect size, heterogeneity of effect sizes, sample size, and the percentage of true null-hypotheses, z = 10.94. Problems mirrored the results for bias. Coverage was low when there were no true null-hypotheses, no heterogeneity in effect sizes, large effects, and small sample sizes. Coverage was only 31.3% (SEMCMC = 2.68) when the percentage of true H0 was 0, heterogeneity of effect sizes was 0, the effect size was Cohen’s d = 0.6, and the sample size was N = 50.
In statistics, it is common to replace confidence intervals that fail to show adequate coverage with confidence intervals that provide good coverage with real data; these confidence intervals are often called robust confidence intervals (Royall, 1996). We suspected that low coverage was related to systematic bias. When confidence intervals are drawn around systematically biased estimates, they are likely to miss the true effect size by the amount of systematic bias, when sampling error pushes estimates in the same direction as the systematic bias. To increase coverage, it is therefore necessary to take systematic bias into account. We created robust confidence intervals by adding three percentage points on each side. This is very conservative because the bias analysis would suggest that only adjustment in one direction is needed.
The logistic regression analysis still showed some statistically significant variation in coverage. The most notable finding was a 2-way interaction for effect size and sample size, z = 4.68. However, coverage was at 95% or higher for all 12 cells of the design. Further inspection showed that the main problem remained scenarios with high effect sizes (d = 0.6) and no heterogeneity (SD = 0), but even with small heterogeneity, SD = 0.2, this problem disappeared. We therefore recommend extending confidence intervals by three percentage points. This is the default setting in the z-curve package, but the package allows researchers to change these settings. Moreover, in meta-analyses of studies with low heterogeneity, alternative methods that are more appropriate for homogeneous methods (e.g., selection models; Hedges, 1992) may be used or the number of components could be reduced.
EDR
Visual inspection of EDRs plotted against the true discovery rates (Figure 4) showed a noticeable increase in uncertainty. This is to be expected as EDR estimates require estimation of the distribution for statistically non-significant z-statistics solely on the basis of the distribution of statistically significant results.
Figure 4. Estimated (y-axis) vs. true (x-axis) EDR across a different number of studies.
Despite the high variability in estimates, they can be useful. With the observed discovery rate in psychology being often over 90% (Sterling, 1959), many of these estimates would alert readers that selection bias is present. A bigger problem is that the highly variable EDR estimates might lack the power to detect selection bias in small sets of studies.
Across all studies, systematic bias was small, 1.42 (SEMCMC = 0.08) for 100 studies, 0.57 (SEMCMC = 0.06) for 300 studies, 0.16 (SEMCMC = 0.05) percentage points for 1000 studies. This shows that the shape of the distribution of statistically significant results does provide valid information about the shape of the full distribution. Consistent with Figure 4, RMSE values were large and remained fairly large even with larger number of studies, 11.70 (SEMCMC = 0.11) for 100 studies, 8.88 (SEMCMC = 0.08) for 300 studies, 6.49 (SEMCMC = 0.07) percentage points for 1000 studies. These results show how costly selection bias is because more precise estimates of the discovery rate would be available without selection bias.
The main consequence of high RMSE is that confidence intervals are expected to be wide. The next analysis examined whether confidence intervals have adequate coverage. This was not the case; coverage = 87.3% (SEMCMC = 0.14). We next used logistic regression to examine patterns in coverage in our simulation design. A notable 3-way interaction between effect size, sample size, and percentage of true H0 was present, z = 3.83. While the pattern was complex, not a single cell of the design showed coverage over 95%.
As before, we created robust confidence intervals by extending the interval. We settled for an extension by five percentage points. The 3-way interaction remained statistically significant, z = 3.36. Now 43 of the 48 cells showed coverage over 95%. For reasons that are not clear to us, the main problem occurred for an effect size of Cohen’s d = 0.4 and no true H0, independent of sample size. While improving the performance of z-curve remains an important goal and future research might find better approaches to address this problem, for now, we recommend using z-curve 2.0 with these robust confidence intervals, but users can specify more conservative adjustments.
Application to Real Data
It is not easy to evaluate the performance of z-curve 2.0 estimates with actual data because selection bias is ubiquitous and direct replication studies are fairly rare (Zwaan, Etz, Lucas, & Donnellan, 2018). A notable exception is the Open Science Collaboration project that replicated 100 studies from three psychology journals (Open Science Collaboration, 2015). This unprecedented effort has attracted attention within and outside of psychological science and the article has already been cited over 1,000 times. The key finding was that out of 97 statistically significant results, including marginally significant ones, only 36 replication studies (37%) reproduced a statistically significant result in the replication attempts.
This finding has produced a wide range of reactions. Often the results are cited as evidence for a replication crisis in psychological science, especially social psychology (Schimmack, 2020). Others argue that the replication studies were poorly carried out and that many of the original results are robust findings (Bressan, 2019). This debate mirrors other disputes about failures to replicate original results. The interpretation of replication studies is often strongly influenced by researchers’ a priori beliefs. Thus, they rarely settle academic disputes. Z-curve analysis can provide valuable information to determine whether an original or a replication study is more trustworthy. If a z-curve analysis shows no evidence for selection bias and a high ERR, it is likely that the original result is credible and the replication failure is a false negative result or the replication study failed to reproduce the original experiment. On the other hand, if there is evidence for selection bias and the ERR is low, replication failures are expected because the original results were obtained with questionable research practices.
Another advantage of z-curve analyses of published results is that it is easier to obtain large representative samples of studies than to conduct actual replication studies. To illustrate the usefulness of z-curve analyses, we focus on social psychology because this field has received the most attention from meta-psychologists (Schimmack, 2020). We fitted z-curve 2.0 to two studies of published test statistics from social psychology and compared these results to the actual success rate in the Open Science Collaboration project (k = 55).
One sample is based on Motyl et al.’s (2017) assessment of the replicability of social psychology (k = 678). The other sample is based on the coding of the most highly cited articles by social psychologists with a high H-Index (k = 2,208; Schimmack, 2021). The ERR estimates were 44%, 95% CI [35, 52]%, and 51%, 95% CI [45, 56]%. The two estimates do not differ significantly from each other, but both estimates are considerably higher than the actual discovery rate in the OSC replication project, 25%, 95% CI [13, 37]%. We postpone the discussion of this discrepancy to the discussion section.
The EDRs estimates were 16%, 95% CI [5, 32]%, and 14%, 95% CI [7, 23]%. Again, both of the estimates overlap and do not significantly differ. At the same time, the EDR estimates are much lower than the ODRs in these two data sets (90%, 89%). The z-curve analysis of published results in social psychology shows a strong selection bias that explains replication failures in actual replication attempts. Thus, the z-curve analysis reveals that replication failures cannot be attributed to problems of the replication attempts. Instead, the low EDR estimates show that many non-significant original results are missing from the published record.
Discussion
A previous article introduced z-curve as a viable method to estimate mean power after selection for significance (Brunner & Schimmack, 2020). This is a useful statistic because it predicts the success rate of exact replication studies. We therefore call this statistic the expected replication rate. Studies with a high replication rate provide credible evidence for a phenomenon. In contrast, studies with a low replication rate are untrustworthy and require additional evidence.
We extended z-curve 1.0 in two ways. First, we implemented the expectation maximization algorithm to fit the mixture model to the observed distribution of z-statistics. This is a more conventional method to fit mixture models. We found that this method produces good estimates, but it did not eliminate some of the systematic biases that were observed with z-curve 1.0. More important, we extended z-curve to estimate the mean power before selection for significance. We call this statistic the expected discovery rate because mean power predicts the percentage of statistically significant results for a set of studies. We found that EDR estimates have satisfactory large sample accuracy, but vary widely in smaller sets of studies. This limits the usefulness for meta-analysis of small sets of studies, but as we demonstrated with actual data, the results are useful when a large set of studies is available. The comparison of the EDR and ODR can also be used to assess the amount of selection bias. A low EDR can also help researchers to realize that they test too many false hypotheses or test true hypotheses with insufficient power.
In contrast to Miller (2009), who stipulates that estimating the ERR (“aggregated replication probability”) is unattainable due to selection processes, Schimmack and Brunner’s (2020) z-curve 1.0 addresses the issue by modeling the selection for significance.
Finally, we examined the performance of bootstrapped confidence intervals in simulation studies. We found that coverage for 95% confidence intervals was sometimes below 95%. To improve the coverage of confidence intervals, we created robust confidence intervals that added three percentage points to the confidence interval of the ERR and five percentage points to the confidence interval of the EDR.
We demonstrate the usefulness of the EDR and confidence intervals with an example from social psychology. We find that ERR overestimates the actual replicability in social psychology. We also find clear evidence that power in social psychology is low and that high success rates are mostly due to selection for significance. It is noteworthy that while the Motyl et al.’s (2017) dataset is representative for social psychology, Schimmack’s (2021) dataset sampled highly influential articles. The fact that both sampling procedures produced similar results suggests that studies by eminent researchers or studies with high citation rates are no more replicable than other studies published in social psychology.
Z-curve 2.0 does provide additional valuable information that was not provided by z-curve 1.0. Moreover, z-curve 2.0 is available as an R-package, making it easier for researchers to conduct z-curve analyses (Bartoš & Schimmack, 2020). This article provides the theoretical background for the use of the z-curve package. Subsequently, we discuss some potential limitations of z-curve 2.0 analysis and compare z-curve 2.0 to other methods that aim to estimate selection bias or power of studies.
Bias Detection Methods
In theory, bias detection is as old as meta-analysis. The first bias test showed that Mendel’s genetic experiments with peas had less sampling error than a statistical model would predict (Pires & Branco, 2010). However, when meta-analysis emerged as a widely used tool to integrate research findings, selection bias was often ignored. Psychologists focused on fail-safe N (Rosenthal, 1979), which did not test for the presence of bias and often led to false conclusions about the credibility of a result (Ferguson & Heene, 2012). The most common tools to detect bias rely on correlations between effect sizes and sample size. A key problem with this approach is that it often has low power and that results are not trustworthy under conditions of heterogeneity (Inzlicht, Gervais, & Berkman, 2015; Renkewitz & Keiner, 2019). The tests are also not useful for meta-analysis of heterogeneous sets of studies where researchers use larger samples to study smaller effects, which also introduces a correlation between effect sizes and sample sizes. Due to these limitations, evidence of bias has been dismissed as inconclusive (Cunningham & Baumeister, 2016; Inzlicht & Friese; 2019).
It is harder to dismiss evidence of bias when a set of published studies has more statistically significant results than the power of the studies warrants; that is, the ODR exceeds the EDR (Sterling et al., 1995). Aside from z-curve 2.0, there are two other bias tests that rely on a comparison of the ODR and EDR to evaluate the presence of selection bias, namely the Test of Excessive Significance (TES, Ioannidis & Trikalinos, 2005) and the Incredibility Test (IT; Schimmack, 2012).
Z-curve 2.0 has several advantages over the existing methods. First, TES was explicitly designed for meta-analysis with little heterogeneity and may produce biased results when heterogeneity is present (Renkewitz & Keiner, 2019). Second, both the TES and the IT take observed power at face value. As observed power is inflated by selection for significance, the tests have low power to detect selection for significance, unless the selection bias is large. Finally, TES and IT rely on p-values to provide information about bias. As a result, they do not provide information about the amount of selection bias.
Z-curve 2.0 overcomes these problems by correcting the power estimate for selection bias, providing quantitative evidence about the amount of bias by comparing the ODR and EDR, and by providing evidence about statistical significance by means of a confidence interval around the EDR estimate. Thus, z-curve 2.0 is a valuable tool for meta-analysts, especially when analyzing a large sample of heterogenous studies that vary widely in designs and effect sizes. As we demonstrated with our example, the EDR of social psychology studies is very low. This information is useful because it alerts readers to the fact that not all p-values below .05 reveal a true and replicable finding.
Nevertheless, z-curve has some limitations. One limitation is that it does not distinguish between significant results with opposite signs. In the presence of multiple tests of the same hypothesis with opposite signs, researchers can exclude inconsistent significant results and estimate z-curve on the basis of significant results with the correct sign. However, the selection of tests by the meta-analyst introduces additional selection bias, which has to be taken into account in the comparison of the EDR and ODR. Another limitation is the assumption that all studies used the same alpha criterion (.05) to select for significance. This possibility can be explored by conducting multiple z-curve analyses with different selection criteria (e.g., .05, .01). The use of lower selection criteria is also useful because some questionable research practices produce a cluster of just significant results. However, all statistical methods can only produce estimates that come with some uncertainty. When severe selection bias is present, new studies are needed to provide credible evidence for a phenomenon.
Predicting Replication Outcomes
Since 2011, many psychologists have learned that published significant results can have a low replication probability (Open Science Collaboration, 2015). This makes it difficult to trust the published literature, especially older articles that report results from studies with small samples that were not pre-registered. Should these results be disregarded because they might have been obtained with questionable research practices? Should results only be trusted if they have been replicated in a new, ideally pre-registered, replication study? Or should we simply assume that most published results are probably true and continue to treat every p-value below .05 as a true discovery?
The appeal of z-curve is that we can use the published evidence to distinguish between credible and “incredible” (biased) statistically significant results. If a meta-analysis shows low selection bias and a high replication rate, the results are credible. If a meta-analysis shows high selection bias and a low replication rate, the results are incredible and require independent verification.
As appealing as this sounds, every method needs to be validated before it can be applied to answer substantive questions. This is also true for z-curve 2.0. We used the results from the OSC replicability project for this purpose. The results suggest that z-curve predictions of replication rates may be overly optimistic. While the expected replication rate was between 44% and 51% (35% – 56% CI range), the actual success rate was only 25%, 95% CI [13, 37]%. Thus, it is important to examine why z-curve estimates are higher than the actual replication rate in the OSC project.
One possible explanation is that there is a problem with the replication studies. Social psychologists quickly criticized the quality of the replication studies (Gilbert, King, Pettigrew, & Wilson, 2016). In response, the replication team conducted the new replications of contested replication studies. Based on the effect sizes in these much larger replication studies, not a single original study would have produced statistically significant results (Ebersole et al., 2020). It is therefore unlikely that the quality of replication studies explains the low success rate of replication studies in social psychology.
A more interesting explanation is that social psychological phenomena are not as stable as boiling distilled water under tightly controlled laboratory conditions. Rather, effect sizes vary across populations, experimenters, times of day, and a myriad of other factors that are difficult to control (Stroebe & Strack, 2014). In this case, selection for significance produces additional regression to the mean because statistically significant results were obtained with the help of favorable hidden moderators that produced larger effect sizes that are unlikely to be present again in a direct replication study.
The worst-case scenario is that studies that were selected for significance are no more powerful than studies that produced statistically non-significant results. In this case, the EDR predicts the outcome of actual replication studies. Consistent with this explanation, the actual replication rate of 25%, 95% CI [13, 37]%, was highly consistent with the EDR estimates of 16%, 95% CI [5, 32]%, and 14%, 95% CI [7, 23]%. More research is needed once more replication studies become available to see how closely actual replication rates are to the EDR and the ERR. For now, they should be considered the worst and the best possible scenarios and actual replication rates are expected to fall somewhere between these two estimates.
A third possibility for the discrepancy is that questionable research practices change the shape of the z-curve in ways that are different from a simple selection model. For example, if researchers have several statistically significant results and pick the highest one, the selection model underestimates the amount of selection that occurred. This can bias z-curve estimates and inflate the ERR and EDR estimates. Unfortunately, it is also possible that questionable research practices have the opposite effect and that ERR and EDR estimates underestimate the true values. This uncertainty does not undermine the usefulness of z-curve analyses. Rather it shows how questionable research practices undermine the credibility of published results. Z-curve 2.0 does not alleviate the need to reform research practices and to ensure that all researchers report their results honestly.
Conclusion
Z-curve 1.0 made it possible to estimate the replication rate of a set of studies on the basis of published test results. Z-curve 2.0 makes it possible to also estimate the expected discovery rate; that is, how many tests were conducted to produce the statistically significant results. The EDR can be used to evaluate the presence and amount of selection bias. Although there are many methods that have the same purpose, z-curve 2.0 has several advantages over these methods. Most importantly, it quantifies the amount of selection bias. This information is particularly useful when meta-analyses report effect sizes based on methods that do not consider the presence of selection bias.
Author Contributions
Most of the ideas in the manuscript were developed jointly. The main idea behind the z-curve method and its density version was developed by Dr. Schimmack. Mr. Bartoš implemented the EM version of the method and conducted the extensive simulation studies.
Acknowledgments
Access to computing and storage facilities owned by parties and projects contributing to the National Grid Infrastructure MetaCentrum provided under the program “Projects of Large Research, Development, and Innovations Infrastructures” (CESNET LM2015042), is greatly appreciated. We would like to thank Maximilian Maier, Erik W. van Zwet, and Leonardo Tozzi for valuable comments on a draft of this manuscript.
No conflict of interest to report. This work was not supported by a specific grant.
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Footnotes
[1] In reality, sampling erorr will produce an observed discovery rate that deviates slightly from the expected discovery rate. To keep things simple, we assume that the observed discovery rate matches the expected discovery rate perfectly.
[2] We thank Erik van Zwet for suggesting this modification in his review and for many other helpful comments.
[3] To compute MCMC standard errors of bias and RMSE across multiple conditions with different true ERR/EDR value, we centered the estimates by substracting the true ERR/EDR. For computing the MCMC standard error of RMSE, we used the Jackknife estimate of variance Efron & Stein (1981).
UPDATE 3/27/2018: Here is R-code to see how z-curve and p-curve work and to run the simulations used by Datacolada and to try other ones. (R-Code download)
Introduction
The blog Datacolada is a joint blog by Uri Simonsohn, Leif Nelson, and Joe Simmons. Like this blog, Datacolada blogs about statistics and research methods in the social sciences with a focus on controversial issues in psychology. Unlike this blog, Datacolada does not have a comments section. However, this shouldn’t stop researchers to critically examine the content of Datacolada. As I have a comments section, I will first voice my concerns about blog post [67] and then open the discussion to anybody who cares about estimating the average power of studies that reported a “discovery” in a psychology journal.
Background:
Estimating power is easy when all studies are honestly reported. In this ideal world, average power can be estimated by the percentage of significant results and with the median observed power (Schimmack, 2015). However, in reality not all studies are published and researchers use questionable research practices that inflate success rates and observed power. Currently two methods promise to correct for these problems and to provide estimates of the average power of studies that yielded a significant result.
Uri Simonsohn’s P-Curve has been in the public domain in the form of an app since January 2015. Z-Curve has been used to critique published studies and individual authors for low power in their published studies on blog posts since June 2015. Neither method has the stamp of approval of peer-review. P-Curve has been developed from Version 3.0 to Version 4.6 without presenting any simulations that the method works. It is simply assumed that the method works because it is built on a peer-reviewed method for the estimation of effect sizes. Jerry Brunner and I have developed four methods for the estimation of average power in a set of studies selected for significance, including z-curve and our own version of p-curve that estimates power and not effect sizes .
We have carried out extensive simulation studies and asked numerous journals to examine the validity of our simulation results. We also posted our results in a blog post and asked for comments. The fact that our work is still not published in 2018 does not reflect problems with out results. The reasons for rejection were mostly that it is not relevant to estimate average power of studies that have been published.
Respondents to an informal poll in the Psychological Methods Discussion Group mostly disagree and so do we.
There are numerous examples on this blog that show how this method can be used to predict that major replication efforts will fail (ego-depletion replicability report) or that claims about the way people (that is you and I) think in a popular book (Thinking: Fast and Slow) for a general audience (again that is you and me) by a Nobel Laureate are based on studies that were obtained with deceptive research practices.
The author, Daniel Kahneman, was as dismayed as I am by the realization that many published findings that are supposed to enlighten us have provided false facts and he graciously acknowledged this.
“I accept the basic conclusions of this blog. To be clear, I do so (1) without expressing an opinion about the statistical techniques it employed and (2) without stating an opinion about the validity and replicability of the individual studies I cited. What the blog gets absolutely right is that I placed too much faith in underpowered studies.” (Daniel Kahneman).
It is time to ensure that methods like p-curve and z-curve are vetted by independent statistical experts. The traditional way of closed peer review in journals that need to reject good work because for-profit publishers and organizations like APS need to earn money from selling print-copies of their journals has failed.
Therefore we ask statisticians and methodologists from any discipline that uses significance testing to draw inferences from empirical studies to examine the claims in our manuscript and to help us to correct any errors. If p-curve is the better tool for the job, so be it.
It is unfortunate that the comparison of p-curve and z-curve has become a public battle. In an idealistic world, scientists would not be attached to their ideas and would resolve conflicts in a calm exchange of arguments. What better field to reach consensus than math or statistics where a true answer exists and can be revealed by means of mathematical proof or simulation studies.
However, the real world does not match the ideal world of science. Just like Uri-Simonsohn is proud of p-curve, I am proud of z-curve and I want z-curve to do better. This explains why my attempt to resolve this conflict in private failed (see email exchange).
The main outcome of the failed attempt to find agreement in private was that Uri Simonsohn posted a blog on Datacolada with the bold claim “P-Curve Handles Heterogeneity Just Fine,” which contradicts the claims that Jerry and I made in the manuscript that I sent him before we submitted it for publication. So, not only did the private communication fail. Our attempt to resolve disagreement resulted in an open blog post that contradicted our claims. A few months later, this blog post was cited by the editor of our manuscript as a minor reason for rejecting our comparison of p-curve and z-curve.
Just to be clear, I know that the datacolada post that Nelson cites was posted after your paper was submitted and I’m not factoring your paper’s failure to anticipate it into my decision (after all, Bem was wrong (Dan Simons, Editor of AMMPS)
Please remember, I shared a document and R-Code with simulations that document the behavior of p-curve. I had a very long email exchange with Uri Simonsohn in which I asked him to comment on our simulation results, which he never did. Instead, he wrote his own simulations to convince himself that p-curve works.
The tweet below shows that Uri is aware of the problem that statisticians can use statistical tricks, p-hacking, to make their method look better than they are.
I will now demonstrate that Uri p-hacked his simulations to make p-curve look better than it is and to hide the fact that z-curve is the better tool for the job.
Critical Examination of Uri Simonsohn’s Simulation Studies
On the blog, Uri Simonsohn shows the Figure below which was based on an example that I provided during our email exchange. The Figure shows the simulated distribution of true power. It also shows the the mean true power is 61%, whereas the p-curve estimate is 79%. Uri Simonssohn does not show the z-curve estimate. He also does not show what the distribution of observed t-values looks like. This is important because few readers are familiar with histograms of power and the fact that it is normal for power to pile up at 1 because 1 is the upper limit for power.
I used the R-Code posted on the Datacolada website to provide additional information about this example. Before I show the results it is important to point out that Uri Simonshon works with a different selection model than Jerry and I. We verified that this has no implications for the performance of p-curve or z-curve, but it does have implications for the distribution of true power that we would expect in real data.
Selection for Significance 1: Jerry and I work with a simple model where researchers conduct studies, test for significance, and then publish the significant results. They may also publish the non-significant results, but they cannot be used to claim a discovery (of course, we can debate whether a significant result implies a discovery, but that is irrelevant here). We use z-curve to estimate the average power of those studies that produced a significant result. As power is the probabilty of obtaining a significant result, the average true power of significant results predicts the success rate in a set of exact replication studies. Therefore, we call this estimate an estimate of replicability.
Selection for Significance 2: The Datacolada team famously coined the term p-hacking. p-hacking refers to massive use of questionable research practices in order to produce statistically significant results. In an influential article, they created the impression that p-hacking allows researchers to get statistical significance in pretty much every study without a real effect (i.e., a false positive). If this were the case, researchers would not have failed studies hidden away like our selection model implies.
No File Drawers: Another Unsupported Claim by Datacolada
In the 2018 volume of Annual Review of Psychology (edited by Susan Fiske), the Datacolada team explicitly claims that psychology researchers do not have file drawers of failed studies.
There is an old, popular, and simple explanation for this paradox. Experiments that work are sent to a journal, whereas experiments that fail are sent to the file drawer (Rosenthal 1979). We believe that this “file-drawer explanation” is incorrect. Most failed studies are not missing. They are published in our journals, masquerading as successes.
They provide no evidence for this claim and ignore evidence to the contrary. For example, Bem (2011) pointed out that it is a common practice in experimental social psychology to conduct small studies so that failed studies can be dismissed as “pilot studies.” In addition, some famous social psychologists have stated explicitly that they have a file drawer of studies that did not work.
“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)
In response to replication failures, Kathleen Vohs acknowledged that a couple of studies with non-significant results were excluded from the manuscript submitted for publication that was published with only significant results.
(2) With regard to unreported studies, the authors conducted two additional money priming studies that showed no effects, the details of which were shared with us. (quote from Rohrer et al., 2015, who failed to replicate Vohs’s findings; see also Vadillo et al., 2016.)
Dan Gilbert and Timothy Wilson acknowledged that they did not publish non-significant results that they considered to be uninformative.
“First, it’s important to be clear about what “publication bias” means. It doesn’t mean that anyone did anything wrong, improper, misleading, unethical, inappropriate, or illegal. Rather it refers to the wellknown fact that scientists in every field publish studies whose results tell them something interesting about the world, and don’t publish studies whose results tell them nothing. Let us be clear: We did not run the same study over and over again until it yielded significant results and then report only the study that “worked.” Doing so would be clearly unethical. Instead, like most researchers who are developing new methods, we did some preliminary studies that used different stimuli and different procedures and that showed no interesting effects. Why didn’t these studies show interesting effects? We’ll never know. Failed studies are often (though not always) inconclusive, which is why they are often (but not always) unpublishable. So yes, we had to mess around for a while to establish a paradigm that was sensitive and powerful enough to observe the effects that we had hypothesized.” (Gilbert and Wilson).
Bias analyses show some problems with the evidence for stereotype threat effects. In a radio interview, Michael Inzlicht reported that he had several failed studies that were not submitted for publication and he is now skeptical about the entirely stereotype threat literature (conflict of interest: Mickey Inzlicht is a friend and colleague of mine who remains the only social psychologists who has published a critical self-analysis of his work before 2011 and is actively involved in reforming research practices in social psychology).
Steve Spencer also acknowledged that he has a file drawer with unsuccessful studies. In 2016, he promised to open his file-drawer and make the results available.
By the end of the year, I will certainly make my whole file drawer available for any one who wants to see it. Despite disagreeing with some of the specifics of what Uli says and certainly with his tone I would welcome everyone else who studies stereotype threat to make their whole file drawer available as well.
Nearly two years later, he hasn’t followed through on this promise (how big can it be? LOL).
Although this anecdotal evidence makes it clear that researchers have file drawers with non-significant results, it remains unclear how large file-drawers are and how often researchers p-hacked null-effects to significance (creating false positive results).
The Influence of Z-Curve on the Distribution of True Power and Observed Test-Statistics
Z-Curve, but not p-curve, can address this question to some extent because p-hacking influences the probability that a low-powered study will be published. A simple selection model with alpha = .05 implies that only 1 out of 20 false positive results produces a significant result and will be included in the set of studies with significant results. In contrast, extreme p-hacking implies that every false positive result (20 out of 20) will be included in the set of studies with significant results.
To illustrate the implications of selection for significance versus p-hacking, it is instructive to examine the distribution of observed significant results based on the simulated distribution of true power in Figure 1.
Figure 2 shows the distribution assuming that all studies will be p-hacked to significance. P-hacking can influence the observed distribution, but I am assuming a simple p-hacking model that is statistically equivalent to optional stopping with small samples. Just keep repeating the experiment (with minor variations that do not influence power to deceive yourself that you are not p-hacking) and stop when you have a significant result.
The histogram of t-values looks very similar to a z-score because t-values with df = 98 are approximately normally distributed. As all studies were p-hacked, all studies are significant with qt(.975,98) = 1.98 as criterion value. However, some studies have strong evidence against the null-hypothesis with t-values greater than 6. The huge pile of t-values just above the criterion value of 1.98 occurs because all low powered studies became significant.
The distribution in Figure 3 looks different than the distribution in Figure 2.
Now there are numerous non-significant results and even a few significant results with the opposite sign of the true effect (t < -1.98). For the estimation of replicability only the results that reached significance are relevant, if only for the reason that they are the only results that are published (success rates in psychology are above 90%; Sterling, 1959, see also real data later on). To compare the distributions it is more instructive to select only the significant results in Figure 3 and to compare the densities in Figures 2 and 3.
The graph in Figure 4 shows that p-hacking results in more just significant results with t-values between 2 and 2.5 than mere publication bias does. The reason is that the significance filter of alpha = .05 eliminates false positives and low powered true effects. As a result the true power of studies that produced significant results is higher in the set of studies that were selected for significance. The average true power of the honest significant results without p-hacking is 80% (as seen in Figure 1, the average power for the p-hacked studies in red is 61%).
With real data, the distribution of true power is unknown. Thus, it is unknown how much p-hacking occurred. For the reader of a journal that reports only significant it is also irrelevant whether p-hacking occurred. A result may be reported because 10 similar studies tested a single hypothesis or 10 conceptual replication studies produced 1 significant result. In either scenario, the reported significant result provides weak evidence for an effect if the significant result occurred with low power.
It is also important to realize (and it took Jerry and I some time to convince ourselves with simulations that this is actually true) that p-curve and z-curve estimates do not depend on the selection mechanism. The only information that matters is the true power of studies and not how studies were selected. To illustrate this fact, I also used p-curve and z-curve to estimate the average power of the t-values without p-hacking (blue distribution in Figure 4). P-Curve again overestimates true power. While average true power is 80%, the p-curve estimate is 94%.
In conclusion, the datacolada blog post did present one out of several examples that I provided and that were included in the manuscript that I shared with Uri. The Datacolada post correctly showed that z-curve provides good estimates of the average true power and that p-curve produces inflated estimates.
I elaborated on this example by pointing out the distinction between p-hacking (all studies are significant) and selection for significance (e.g., due to publication bias or in assessing replicability of published results). I showed that z-curve produces the correct estimates with and without p-hacking because the selection process does not matter. The only consequence of p-hacking is that more low-powered studies become significant because it undermines the function of the significance filter to prevent studies with weak evidence from entering the literature.
In conclusion, the actual blog post shows that p-curve can be severely biased when data are heterogeneous, which contradicts the title that P-Curve handles heterogeneity just fine.
When The Shoe Doesn’t Fit, Cut of Your Toes
To rescue p-curve and to justify the title, Uri Simonsohn suggests that the example that I provided is unrealistic and that p-curve performs as well or better in simulations that are more realistic. He does not mention that I also provided real world examples in my article that showed better performance of z-curve with real data.
So, the real issue is not whether p-curve handles heterogeneity well (it does not). The real issue is now how much heterogeneity we should expect.
Figure 5 shows that Uri Simonsohn considers to be realistic data. The distribution of true power uses the same beta distribution as the distribution in Figure 1, but instead of scaling it from the lowest possible value (alpha = 5%) to the highest possible value 1-1/infinity), it scales power from alpha to a maximum of 80%. For readers less familiar with power, a value of 80% implies that researches plan studies deliberately with the risk of a 20% probability to end up with a false negative result (i.e., the effect exists, but the evidence is not strong enough, p > .05).
The labeling in the graph implies that studies with more than recommended 80% power, including 81% power are considered to have extremely high power (again, with a 20% risk of a false positive result). The graph also shows that p-curve provided an unbiased estimate of true average power despite (extreme) heterogeneity in true power between 5% and 80%.
Figure 6 shows the histogram of observed t-values based on a simulation in which all studies in Figure 5 are p-hacked to get significance. As p-hacking inflates all t-values to meet the minimum value of 1.98, and truncation of power to values below 80% removes high t-values, 92% of t-values are within the limited range from 1.98 to 4. A crud measure of heterogeneity is the variance of t-values, which is 0.51. With N = 100, a t-distribution is just a little bit wider than the standard normal distribution, which has a standard deviation of 1. Thus, the small variance of 0.51 indicates that these data have low variability.
The histogram of observed t-values and the variance in these observed t-values makes it possible to quantify heterogeneity in true power. In Figure 2, heterogeneity was high (Var(t) = 1.56) and p-curve overestimated average true power. In Figure 6, heterogeneity is low (Var(t) = 0.51) and p-curve provided accurate estimates. This finding suggests that estimation bias in p-curve is linked to the distribution and variance in observed t-values, which reflects the distribution and variance in true power.
When the data are not simulated, test statistics can come from different tests with different degrees of freedom. In this case, it is necessary to convert all test statistics into z-scores so that strength of evidence is measured in a common metric. In our manuscript, we used the variance of z-scores to quantify heterogeneity and showed that p-curve overestimates when heterogeneity is high.
In conclusion, Uri Simonsohn demonstrated that p-curve can produce accurate estimates when the range of true power is arbitrarily limited to values below 80% power. He suggests that this is reasonable because having more than 80% power is extremely high power and rare.
Thus, there is no disagreement between Uri Simonsohn and us when it comes to the statistical performance of p-curve and z-curve. P-curve overestimates when power is not truncated at 80%. The only disagreement concerns the amount of actual variability in real data.
What is realistic?
Jerry and I are both big fans of Jacob Cohen who has made invaluable contributions to psychology as a science, including his attempt to introduce psychologists to Neyman-Pearson’s approach to statistical inferences that avoids many of the problems of Fishers’ approach that dominates statistics training in psychology to this day.
The concept of statistical power requires that researchers formulate an alternative hypothesis, which requires specifying an expected effect size. To facilitate this task, Cohen developed standardized effect sizes. For example, Cohen’s standardizes a mean difference (e.g., height difference between men and women in centimeters) by the standard deviation. As a result, the effect size is independent of the unit of measurement and is expressed in terms of percentages of a standard deviation. Cohen provided rough guidelines about the size of effect sizes that one could expect in psychology.
It is now widely accepted that most effect sizes are in the range between 0 and 1 standard deviation. It is common to refer to effect sizes of d = .2 (20% of a standard deviation) as small, d = .5 as medium, and d = .8 as large.
True power is a function of effect size and sampling error. In a between subject study sampling error is a function of sample size and most sample sizes in between-subject designs fall into a range from 40 to 200 participants, although sample sizes have been increasing somewhat in response to the replication crisis. With N = 40 to 200, sampling error ranges from 0.14 (2/sqrt(200) to .32 (2/sqrt(40).
The non-central t-values are simply the ratio of standardized effect sizes and sampling error of standardized measures. At the lowest end, effect sizes of 0 have a non-central t-value of 0 (0/.14 = 0; 0/.32 = 0). At the upper end, a large effect size of .8 obtained in the largest sample (N = 200) yields a t-value of .8/.14 = 5.71. While smaller non-central t-values than 0 are not possible, larger non-central t-values can occur in some studies. Either the effect size is very large or sampling error is smaller. Smaller sampling errors are especially likely when studies use covariates, within-subject designs or one-sample t-tests. For example, a moderate effect size (d = .5) in a within-subject design with 90% fixed error variance (r = .9), yields a non-central t-value of 11.
A simple way to simulate data that are consistent with these well-known properties of results in psychology is to assume that the average effect size is half a standard deviation (d = .5) and to model variability in true effect sizes with a normal distribution with a standard deviation of SD = .2. Accordingly, 95% of effect sizes would fall into the range from d = .1 to d = .9. Sample sizes can be modeled with a simple uniform distribution (equal probability) from N = 40 to 200.
Converting the non-centrality parameters to power with p < .05 shows that many values fall into the region from .80 to 1 that Uri Simonsohn called extremely high power. The graph shows that it does not require extremely large effect sizes (d > 1) or large samples (N > 200) to conduct studies with 80% power or more. Of course, the percentage of studies with 80% power or more depends on the distribution of effect sizes, but it seems questionable to assume that studies rarely have 80% power.
The mean true power is 66% (I guess you see where this is going).
This is the distribution of the observed t-values. The variance is 1.21 and 23% of the t-values are greater than 4. The z-curve estimate is 66% and the p-curve estimate is 83%.
In conclusion, a simulation that starts with knowledge about effect sizes and sample sizes in psychological research shows that it is misleading to call 80% power or more extremely high power that is rarely achieved in actual studies. It is likely that real datasets will include studies with more than 80% power and that this will lead p-curve to overestimate average power.
A comparison of P-Curve and Z-Curve with Real Data
The point of fitting p-curve and z-curve to real data is not to validate the methods. The methods have been validated in simulation studies that show good performance of z-curve and poor performance of p-curve when hterogeneity is high.
The only question remains how biased p-curve is with real data. Of course, this depends on the nature of the data. It is therefore important to remember that the Datacolada team proposed p-curve as an alternative to Cohen’s (1962) seminal study of power in the 1960 issue of the Journal of Abnormal and Social Psychology.
“Estimating the publication-bias corrected estimate of the average power of a set of studies can be useful for at least two purposes. First, many scientists are intrinsically interested in assessing the statistical power of published research (see e.g., Button et al., 2013; Cohen, 1962; Rossi, 1990; Sedlmeier & Gigerenzer, 1989).
There have been two recent attempts at estimating the replicability of results in psychology. One project conducted 100 actual replication studies (Open Science Collaboration, 2015). A more recent project examined the replicability of social psychology using a larger set of studies and statistical methods to assess replicability (Motyl et al., 2017).
The authors sampled articles from four journals, the Journal of Personality and Social Psychology, Personality and Social Psychology Bulletin, Journal of Experimental Psychology, and Psychological Science and four years, 2003, 2004, 2013, and 2014. They randomly sampled 543 articles that contained 1,505 studies. For each study, a coding team picked one statistical test that tested the main hypothesis. The authors converted test-statistics into z-scores and showed histograms for the years 2003-2004 and 2013-2014 to examine changes over time. The results were similar.
The histograms show clear evidence that non-significant results are missing either due to p-hacking or publication bias. The authors did not use p-curve or z-curve to estimate the average true power. I used these data to examine the performance of z-curve and p-curve. I selected only tests that were coded as ANOVAs (k = 751) or t-tests (k = 232). Furthermore, I excluded cases with very large test statistics (> 100) and experimenter degrees of freedom (10 or more). For participant degrees of freedom, I excluded values below 10 and above 1000. This left 889 test statistics. The test statistics were converted into z-scores. The variance of the significant z-scores was 2.56. However, this is due to a long tail of z-scores with a maximum value of 18.02. The variance of z-scores between 1.96 and 6 was 0.83.
Fitting z-curve to all significant z-scores yielded an estimate of 45% average true power. The p-curve estimate was 78% (90%CI = 75;81). This finding is not surprising given the simulation results and the variance in the Motyl et al. data.
One possible solution to this problem could be to modify p-curve in the same way that z-curve only models z-scores between 1.96 and 6 and treats all z-scores of 6 as having power = 1. The z-curve estimate is then adjusted by the proportion of extreme z-scores
Using the same approach with p-curve does help to reduce the bias in p-curve estimates, but p-curve still produces a much higher estimate than z-curve, namely 63% (90%CI = .58;67. This is still nearly 20% higher than the z-curve estimate.
In response to these results, Leif Nelson argued that the problem is not with p-curve, but with the Motyl et al. data.
One of these “clearly invalid” data are the data from Motyl et al.’s study. Nelson claim is based on another datacolada blog post about the Motyl et al. study with the title
A detailed examination of datacolada 60 will be the subject of another open discussion about Datacolada. Here it is sufficient to point that Nelson’s strong claim that Motyl et al.’s data are “clearly invalid” is not based on empirical evidence. It is based on disagreement about the coding of 10 out of over 1,500 tests (0.67%). Moreover, it is wrong to label these disagreements mistakes because there is no right or wrong way to pick one test from a set of tests.
In conclusion, the Datacolada team has provided no evidence to support their claim that my simulations are unrealistic. In contrast, I have demonstrated that their truncated simulation does not match reality. Their only defense is now that I cheery-picked data that make z-curve look good. However, a simulation with realistic assumptions about effect sizes and sample sizes also shows large heterogeneity and p-curve fails to provide reasonable estimates.
The fact that sometimes p-curve is not biased is not particularly important because z-curve provides practically useful estimates in these scenarios as well. So, the choice is between one method that gets it right sometimes and another method that gets it right all the time. Which method would you choose?
It is important to point out that z-curve shows some small systematic bias in some situations. The bias is typically about 2% points. We developed a conservative 95%CI to address this problem and demonstrated that his 95% confidence interval has good coverage under these conditions and is conservative in situations when z-curve is unbiased. The good performance of z-curve is the result of several years of development. Not surprisingly, it works better than a method that has never been subjected to stress-tests by the developers.
Future Directions
Z-curve has many additional advantages over p-curve. First, z-curve is a model for heterogeneous data. As a result, it is possible to develop methods that can quantify the amount of variability in power while correcting for selection bias. Second, heterogeneity implies that power varies across studies. As studies with higher power tend to produce larger z-scores, it is possible to provide corrected power estimates for sets of z-values. For example, the average power of just significant results (z < 2.5) could be very low.
Although these new features are still under development, first tests show promising results. For example, the local power estimates for Motyl et al. suggest that test statistics with z-scores below 2.5 (p = .012) have only 26% power and even those between 2.5 and 3.0 (p = .0026) have only 34% power. Moreover, test statistics between 1.96 and 3 account for two-thirds of all test statistics. This suggests that many published results in social psychology will be difficult to replicate.
The problem with fixed-effect models like p-curve is that the average may be falsely generalized to individual studies. Accordingly, an average estimate of 45% might be misinterpreted as evidence that most findings are replicable and that replication studies with a little bit power would be able to replicate most findings. However, this is not the case (OSC, 2015). In reality, there are many studies with low power that are difficult to replicate and relatively few studies with very high power that are easy to replicate. Averaging across these studies gives the wrong impression that all studies have moderate power. Thus, p-curve estimates may be misinterpreted easily because p-curve ignores heterogeneity in true power.
Final Conclusion
In the datacolada 67 blog post, the Datacolada team tried to defend p-curve against evidence that p-curve fails when data are heterogeneous. It is understandable that authors are defensive about their methods. In this comment on the blog post, I tried to reveal flaws in Uri’s arguments and to show that z-curve is indeed a better tool for the job. However, I am just as motivated to promote z-curve as the Datacolada team is to promote p-curve.
To address this problem of conflict of interest and motivated reasoning, it is time for third parties to weigh in. Neither method has been vetted by traditional peer-review because editors didn’t see any merit in p-curve or z-curve, but these methods are already being used to make claims about replicability. It is time to make sure that they are used properly. So, please contribute to the discussion about p-curve and z-curve in the comments section. Even if you simply have a clarification question, please post it.
“For generalization, psychologists must finally rely, as has been done in all the older sciences, on replication” (Cohen, 1994).
DEFINITION OF REPLICABILITY: In empirical studies with sampling error, replicability refers to the probability of a study with a significant result to produce a significant result again in an exact replication study of the first study using the same sample size and significance criterion (Schimmack, 2017).
See Reference List at the end for peer-reviewed publications.
Mission Statement
The purpose of the R-Index blog is to increase the replicability of published results in psychological science and to alert consumers of psychological research about problems in published articles.
To evaluate the credibility or “incredibility” of published research, my colleagues and I developed several statistical tools such as the Incredibility Test (Schimmack, 2012); the Test of Insufficient Variance (Schimmack, 2014), and z-curve (Version 1.0; Brunner & Schimmack, 2020; Version 2.0, Bartos & Schimmack, 2021).
I have used these tools to demonstrate that several claims in psychological articles are incredible (a.k.a., untrustworthy), starting with Bem’s (2011) outlandish claims of time-reversed causal pre-cognition (Schimmack, 2012). This article triggered a crisis of confidence in the credibility of psychology as a science.
Over the past decade it has become clear that many other seemingly robust findings are also highly questionable. For example, I showed that many claims in Nobel Laureate Daniel Kahneman’s book “Thinking: Fast and Slow” are based on shaky foundations (Schimmack, 2020). An entire book on unconscious priming effects, by John Bargh, also ignores replication failures and lacks credible evidence (Schimmack, 2017). The hypothesis that willpower is fueled by blood glucose and easily depleted is also not supported by empirical evidence (Schimmack, 2016). In general, many claims in social psychology are questionable and require new evidence to be considered scientific (Schimmack, 2020).
Each year I post new information about the replicability of research in 120 Psychology Journals (Schimmack, 2021). I also started providing information about the replicability of individual researchers and provide guidelines how to evaluate their published findings (Schimmack, 2021).
Replication is essential for an empirical science, but it is not sufficient. Psychology also has a validation crisis (Schimmack, 2021). That is, measures are often used before it has been demonstrate how well they measure something. For example, psychologists have claimed that they can measure individuals’ unconscious evaluations, but there is no evidence that unconscious evaluations even exist (Schimmack, 2021a, 2021b).
If you are interested in my story how I ended up becoming a meta-critic of psychological science, you can read it here (my journey).
References
Brunner, J., & Schimmack, U. (2020). Estimating population mean power under conditions of heterogeneity and selection for significance. Meta-Psychology, 4, MP.2018.874, 1-22 https://doi.org/10.15626/MP.2018.874
Schimmack, U. (2012). The ironic effect of significant results on the credibility of multiple-study articles. Psychological Methods, 17, 551–566 http://dx.doi.org/10.1037/a0029487
Schimmack, U. (2020). A meta-psychological perspective on the decade of replication failures in social psychology. Canadian Psychology/Psychologie canadienne, 61(4), 364–376. https://doi.org/10.1037/cap0000246
