In a blog post on Andrew Gelman’s blog, Erik van Zwet voiced serious concerns about the performance of z-curve, a meta-analytic method to detect selection bias. The main concern was that z-curve failed to detect selection bias in a scenario where most observed data come from high-powered studies (noncentrality parameter z = 4) but some come from tests of true H0 (effect size is zero, z = 0). In some cases, there may only be a couple of false positive results and that provides too little information about the file drawer of missing tests of H0).
The first problem that I already addressed is that EvZ’s criticism was invalid because it generalized from a single unrealistic scenario to all other situations and did not mention that z-curve had been validated and performed well in these situations (Schimmack, 2026).
Another selection bias in EvZ’s criticism of z-curve is that he only examined the performance of z-curve and did not compare it to the performance of other models. One advantage of z-curve is that it works even if there is little or no variation in sample sizes, which is a requirement for all regression based methods like Funnel plots, Eggert regression, or PET/PEESE. Thus, the most relevant competitor for z-curve are selection models like Vevea and Wood’s (2005) random-effects, step-function model implemented in the r-package weightr.
I tested the model using the same simulation design that was used to examine the performance of z-curve with identical data. Here I focus on the EvZ scenario where most statistically significant results come tests with high power (d = .6, N = 200, z ~ 4.24, power ~ 98%). Thus, there are few non-significant results that can be suppressed by publication bias.
All simulations had 70% selection bias. That is only 30% of the non-significant results were reported and the distribution was flat. First I examined the performance of weightr with k = 100 significant results. All 100 simulations failed to provide estimates of the selection weight for non-significant results. With k = 300 significant results, bias was detected 92% of the time. With k = 1,000, bias was detected in all 100 simulations.
I then examined performance when 20% of the significant results are false positives – and the other 80% come from the same high-powered distribution as before. Figure 1 shows results for a run with k = 1,000 significant results for z-curve. With k = 1,000 z-curve has no problem detecting the selection bias because the distribution of the significant results is clearly bimodal with the mode for the studies with weak power in the non-significant range. Z-curve shows that there are more observed significant results, observed discover rate ODR = 47% than z-curve predicts based on the distribution of the significant results, expected discovery rate, EDR = 23%. The difference is highly significant, p < .000001.
In contrast, the step-function model falsely interprets the higher percentage of non-significant results as evidence that significant results are missing, w(p-value in .025 to .5 range) = 2.24, 95% 2.05 to 2.43. The reason is that the model does not allow for bimodal distributions and assumes a normal distribution of effect sizes, which also implies a normal distribution of z-values when sample sizes are fixed. This problem with the step-function selection model was already reported by Hedges & Vevea (1995). When the simulated data matched the assumed normal distribution, the model worked well. When the distribution did not match the assumed distribution, the model produced bias estimates. The advantage of z-curve is that it does not make a strong distribution assumption and allows for bimodal distributions like the one in Figure 1.
Conclusion
This blog post shows further evidence that EvZ’ expression of concerns about z-curve are biased and do not provide a balanced account of the strengths and weaknesses of z-curve. It is unreasonable to expect a model to perform well in an edge case that also provides problems for other models. In fact, z-curve handles the problem of bimodal distributions better than other models that assume unimodal distributions. If a heterogeneous literature contains a mixture of studies that tested true and false hypotheses, z-curve is actually the superior method and there are no alternatives because most meta-analytic methods were designed to analyze data where all studies are fairly similar and variation in population effect sizes is small. However, many meta-analyses in psychology show evidence of large heterogeneity and the true distribution of effect sizes across studies is unknown. For these kind of data, z-curve is currently the most appropriate statistical tool.
The caliper test is a statistical method for detecting publication bias introduced by Gerber and Malhotra (2008a, 2008b). It tests whether the distribution of test statistics is continuous and approximately locally symmetric around a significance threshold, typically z = 1.96, corresponding to p = .05. The key assumption is that, in the absence of publication bias or p-hacking, the expected density of z-scores in a narrow band just above the threshold should be approximately equal to the expected density just below it. A significant excess of results just above the threshold suggests that researchers or publication processes have shifted results across the boundary, either through selective reporting or analytical flexibility.
Procedure
Published p-values are converted to z-scores (z = Φ⁻¹(1 − p/2)). A caliper of width w is placed symmetrically around the threshold, creating two bins: one from 1.96 to 1.96 + w (just significant) and one from 1.96 − w to 1.96 (just nonsignificant). Under the null hypothesis of no bias, the counts in the two bins should be equal. The test is conducted as a one-sided binomial test with expected probability 0.50. Gerber and Malhotra (2008a) recommended bandwidths of 5%, 10%, 15%, and 20% of the threshold value. A 10% caliper around z = 1.96, for example, compares counts in the intervals [1.764, 1.96) and [1.96, 2.156].
Applications
Gerber and Malhotra applied the caliper test to leading political science journals (APSR, AJPS) and sociology journals (ASR, AJS) and found strong evidence of publication bias (Gerber & Malhotra, 2008a; Gerber & Malhotra, 2008b). The test was subsequently adopted in economics, most notably by Brodeur, Lé, Sangnier, and Zylberberg (2016) and Brodeur, Cook, and Heyes (2020), who documented significant bunching of test statistics just above conventional thresholds across top economics journals. Berning and Weiß (2016) applied the caliper test to German social science journals, again finding evidence of bias. The test has become a standard tool in the meta-science toolkit for discipline-wide assessments of publication practices.
Strengths
The caliper test has several practical advantages. The logic is intuitive and easy to communicate. It requires only test statistics or p-values, not standardized effect sizes, making it applicable to heterogeneous literatures where effect-size metrics vary across studies and designs. For discipline-wide analyses where studies address different research questions with different effects, the caliper test avoids the strong assumptions about comparability or homogeneity required by many other methods.
Limitations
The caliper test’s local-symmetry assumption is exact for normally distributed z-values only when the noncentrality parameter equals the critical value. For the conventional threshold z = 1.96, this corresponds to a study with approximately 50% power. If power is lower, the expected distribution slopes downward across the threshold, producing more just-nonsignificant than just-significant results. If power is higher, the distribution slopes upward across the threshold, producing more just-significant than just-nonsignificant results even in the absence of publication bias. Thus, deviations from caliper symmetry can reflect the power distribution of studies rather than selective publication or p-hacking.
This vulnerability becomes more influential with wider caliper intervals. With negative slopes near the threshold, as in low-powered settings, the assumption of local flatness reduces the power of the caliper test to detect publication bias. With positive slopes near the threshold, as in high-powered settings, there are more observations in the interval above the criterion value than below it even without bias. Thus, the caliper test can falsely identify publication bias when the literature has high power or when the mixture distribution slopes upward around the significance threshold. It is therefore unclear whether positive caliper-test results in some applications reflect bias or the expected shape of the z-value distribution.
Schneck (2017) conducted a Monte Carlo simulation comparing the caliper test to Egger’s test, p-uniform, and the test for excess significance (TES). He found that the 5% caliper maintained acceptable false-positive rates but had low power with fewer than 1,000 studies. The 10% and 15% calipers showed inflated false-positive rates at large K, because wider calipers span a larger portion of the density curve where the local-uniformity assumption can break down. Schneck recommended the 5% caliper for discipline-wide analyses with large K. However, a small caliper does not solve the problem of true asymmetric distributions. With large K, even small departures from local symmetry can be estimated precisely, and the caliper test can become significant even if there is no publication bias.
Simulation studies using z-curve’s heterogeneous effect-size framework reveal the problem more starkly. In a simulation with high average power, fewer than 200 studies, and no bias, the caliper test detected bias 100% of the time. Thus, the test should not be interpreted as evidence of publication bias without inspecting the expected or observed shape of the z-value distribution.
This is not merely a calibration problem that can be fixed by adjusting the significance level or caliper width. Narrower calipers can reduce curvature-induced artifacts, but they cannot remove the conceptual mismatch between what the test assumes, local symmetry, and the actual distribution of z-values when the density slopes across the threshold.
This limitation is not shared by all bias-detection methods. Methods that model the full distribution of z-scores, such as z-curve (Brunner & Schimmack, 2020; Bartoš & Schimmack, 2022), can estimate the expected shape of the z-value distribution under heterogeneous power and selection. The advantage of the caliper test is that it can have high power to detect threshold-related discontinuities in some conditions. Its disadvantage is that it can also provide false evidence of bias when the expected distribution is asymmetric. Therefore, the caliper test should be used together with a plot of the z-value distribution. A positive slope for significant values is a red flag because it violates the local-symmetry assumption of the caliper test.
Summary
The caliper test is a simple, widely used tool for detecting threshold-related publication bias in large literatures. It is most reliable when the expected distribution of test statistics is approximately locally symmetric around the significance threshold in the absence of bias. In literatures where the z-value distribution slopes across the threshold — whether because of high power, low power, or heterogeneous true effects — the test can mistake the expected shape of the distribution for evidence of selective publication or p-hacking. This problem is especially relevant in discipline-wide analyses in the social sciences, where studies often address different hypotheses, use different designs, and have heterogeneous statistical power. Researchers using the caliper test in such settings should interpret positive results with caution and consider model-based alternatives that account for the expected shape of the z-score distribution.
References
Bartoš, F., & Schimmack, U. (2022). Z-curve 2.0: Estimating replication rates and discovery rates. Meta-Psychology, 6, MP.2020.2720.
Berning, C. C., & Weiß, B. (2016). Publication bias in the German social sciences: An application of the caliper test to three top-tier German social science journals. Quality & Quantity, 50, 901–917.
Brodeur, A., Cook, N., & Heyes, A. (2020). Methods matter: p-hacking and publication bias in causal analysis in economics. American Economic Review, 110(11), 3634–3660.
Brodeur, A., Lé, M., Sangnier, M., & Zylberberg, Y. (2016). Star Wars: The empirics strike back. American Economic Journal: Applied Economics, 8(1), 1–32.
Brunner, J., & Schimmack, U. (2020). Estimating population mean power under conditions of heterogeneity and selection for significance. Meta-Psychology, 4, MP.2018.874.
Gerber, A. S., & Malhotra, N. (2008a). Do statistical reporting standards affect what is published? Publication bias in two leading political science journals. Quarterly Journal of Political Science, 3(3), 313–326.
Gerber, A. S., & Malhotra, N. (2008b). Publication bias in empirical sociological research: Do arbitrary significance levels distort published results? Sociological Methods & Research, 37(1), 3–30.
Gerber, A. S., Malhotra, N., Dowling, C. M., & Doherty, D. (2010). Publication bias in two political behavior literatures. American Politics Research, 38(4), 591–613.
Schneck, A. (2017). Examining publication bias — a simulation-based evaluation of statistical tests on publication bias. PeerJ, 5, e4115.
Power Failure, False Positives, and The Replication Crisis
Scientists have become increasingly skeptical about the credibility of published results (Baker, 2016). The main concern is that scientists were presenting results as objective facts, while the results were often influenced by undisclosed subjective decisions that increased the chances of presenting a desirable result. These degrees of freedom in analyses are now called questionable research practices or p-hacking.
Ioannidis (2005) showed with hypothetical scenarios that questionable research practices combined with low statistical power and testing of many false hypotheses could lead to more false than true discoveries of statistical regularities (i.e., a statistically significant result).
Awareness of this problem has produced thousands of new articles that discuss this problem. It has even created its own new science called meta-science; the scientific study of science. Some articles have gained prominent status and are foundational to meta-science.
For example, the Reproducibility Project in psychology replicated 100 studies. While 97 of these studies reported a statistically significant result, only 36% of the replication studies showed a significant result. The drop in the success rate can be attributed to questionable research practices that inflated effect size estimates to achieve significance. Honest replications did not have this advantage, and the true population effect sizes were often too small to produce significant results.
The true probability of obtaining a statistically significant result is called statistical power (Cohen, 1988; Neyman & Pearson, 1933). In the long run, a set of studies with average true power of 50% are expected to produce 50% significant results, even if all studies test different hypotheses (Brunner & Schimmack, 2020l). Thus, the success rate of the Reproducibility Project implies that the replication studies had about 40% average power. As these studies replicated original studies as closely as possible (and similar sample sizes), this suggests that the average power of the original studies was also around 40%.
This estimate is in line with Cohen’s (1962) seminal estimate of power. Average power around 40% has two implications. First, many attempts to demonstrate an effect in a single study will fail to reject a false null hypothesis that there is no relationship; a false negative result (Cohen, 1988). Concerns about false negatives were the focus of meta-scientific discussions about significance testing in the 1990s (Cohen, 1994).
This shifted, when meta-scientists pointed out the consequences of selection for significance and low power (Ioannidis, 2005; Rosenthal, 1979; Sterling et al., 1995). Low statistical power combined with questionable research practices could result in many false discoveries (i.e., statistically significant results without a real effect). In some scenarios, literatures could be entirely made up of false discoveries (Rosenthal, 1979) or at least more false than true discoveries (Ioannidis, 2005).
Theoretical articles and simulation studies suggested that false positive rates might be uncomfortably high and replication failures seemed to support this suspicion, although replication failures could also just be false negative results (Maxwell, 2016). Thus, actual replication studies often do not settle conflicting interpretations of the evidence. While some researchers see replication failures as evidence that original results cannot be trusted, others point towards the difficulty of replicating actual studies and false negatives as reasons why original results could not be replicated (Gilbert et al., 2016).
An alternative approach examines false positives for sets of studies rather than a single study. The statistical results of original articles are used to estimate the average power of studies and to use power to evaluate the risk of false positive results. One of the first attempts to do so was Button, Ioannidis, Mokrysz, Nosek, Flint, Robinson, and Munafò’s (2013) article “Power failure: why small sample size undermines the reliability of neuroscience.” The key empirical finding was that median power of 730 studies from 49 meta-analysis was 21%. The article did not provide an empirical estimate of the false positive rate, but it did illustrate implications of the power estimate for false positive rates in various scenarios. The authors suggested that “a major implication is that the likelihood that any nominally significant finding actually reflects a true effect is small” (p. 371). This claim has contribute to concerns that many published significant results are unreliable.
Reexamining The Power Failure
More than ten years later, it is possible to revisit the seminal article with the benefit of hindsight. Advances in the estimation of true power have revealed important conceptual problems that are different from the computation of hypothetical power for the purpose of sample size planning (Brunner & Schimmack, 2020; Soto & Schimmack, 2026).
Cohen defined statistical power as the probability of obtaining a significant result (1988). In the context of sample size planning, however, power is defined as the probability of obtaining a significant result given a hypothetical population effect size greater than zero. This conditional definition of power given a true hypothesis is widely used in the power literature and was also used by Ioannidis (2005) in his calculations of false positive rates.
Assuming only true hypothesis to compute power is reasonable for hypothetical scenarios, but not for the estimation of true power of completed studies. As the population effect size remains unknown after a study produced an effect size estimate, it is not possible to assume an effect size greater than zero. Thus, the true probability of a completed study to produce a significant result is unconditional and independent of the distinction between H0 and H1. Any estimate of average true power is therefore an estimate of the unconditional probability to produce a significant result. This average can contain tests of true null-hypothesis.
The distinction between conditional and unconditional probabilities has important implications for Button’s calculations of false positive rates. The median power of 21% is unconditional, but the false positive calculations assume conditional power. This can lead to inflated estimates of false positive rates. For example, mean power of 20% could be made up of 50% true H0 with a 5% probability to produce a (false) significant results and 50% tests of H1 with 35% power. In this scenario, the false positive rate is 2.5% / (2.5% + 17.5) = 12.5%. Increasing the proportion of true hypothesis that were tested to a 4:1 ratio would increase the conditional power of tests of H1 to 80% to maintain 20% average power. The false positive rate would increase to .04 / (.04 + .15) = 20%. As noted by Soric (1989), we can even compute the maximum false positive rate that is consistent with unconditional mean power assuming conditional power of 1. With mean power of 21%, the maximum ratio of H0 over H1 is 5.25:1 and the maximum false discovery rate is 20%.
Table 1
Maximum False Discovery Rate for 20% Unconditional Power (Soric, 1989)
Not Significant
Significant
Total
H₁ True
.000
.160
.160
H₀ True
.798
.042
.840
Total
.798
.202
1.000
H₀ : H₁ Ratio
5.25 : 1
False Discovery Rate
.208
Note. The table shows the maximum false discovery rate when average unconditional power equals 20%. This maximum occurs when conditional power for true hypotheses (H₁) equals 100%. The false discovery rate equals the proportion of significant results that are false positives: .042 / .202 = .208. Any lower conditional power with the same unconditional power of 20% produces a lower false discovery rate.
The 21% false positive rate overestimates the true false positive rate with 21% median power for two reasons. Soric’s formula assumes that H1 are tested with 100% power. Assuming that many tests of small true effect sizes in small samples have low conditional power, the true false positive rate is below 21%. The second reason is that unconditional power has a skewed distribution with many low power studies and a few high power studies. As a result, mean power will be higher than median power. Button et al.’s provide information about mean power based on their analyses of publication bias that uses mean power. This analysis suggested that 254 of the 730 studies were expected to produce a significant result and the expected percentage of significant results is equivalent to mean power (Brunner & Schimmack, 2020). Thus, mean power was estimated to be 254 / 730 = 35%. Based on Soric’s formula, the maximum false discovery rate with 35% significant results is 10%.
In conclusion, Button et al.’s estimate of unconditional mean power can be used to draw inferences about false positives in the meta-analyses that they examined that do not rely on unknown ratios of true and false hypotheses being tested in neuroscience. Using their data and Soric’s formula suggests that the false positive risk is fairly small.
A Z-Curve Analyses of Button et al.’s Data
Button et al.’s article contribute to a culture of open sharing of data, but that was not the norm when the article was published. Fortunately, Nord et al. (2017) conducted further analyses of the data and shared power estimates for the 730 studies in an Open Science Foundation (OSC) project. The power estimates do not use the effect sizes of individual studies. Rather they use the sample sizes and the meta-analytic effect size to estimate power. This approach corrects for effect size inflation in smaller studies and reduces bias in power estimates. The following analyses used these data. Power estimates based on individual studies are likely to be inflated by publication bias.
Based on these data, 28% of the studies were statistically significant. Mean power was 35%, matching Button et al.’s estimate of mean power, suggesting that Nord et al.’s power values are based on meta-analytic effect sizes.
I converted power values into z-values and analyzed the z-values with z-curve.3.0 using the default model (Figure 1).
The observed discovery rate (ODR) is simply the percentage of significant results. More important is the bias-corrected estimate of unconditional mean power for all 730 z-values. Z-curve uses the observed distribution of significant z-values and projects the fitted model into the range of unobserved significant results. As shown in Figure 1, the model predicts the actual distribution of non-significant results fairly well. This suggests that the use of meta-analytic effect sizes adjusted inflated effect size estimates and removed publication bias. The estimated mean power for all studies is called the expected discovery rate (EDR). The EDR estimate is close to the ODR, suggesting further that the data are unbiased.
A key problem of estimating the EDR based on the significant results only is that the confidence interval around the point estimate is very wide. When the data show no major bias, more precise estimates can be obtained by fitting the model to all 730 data (Figure 2).
The key finding is that the point estimate of the false positive risk, FDR = 13% is in line with calculations based on Button’s estimate of mean power. The confidence interval around this estimate limits the FDR at 20%. This is an upper limit because conditional power of studies with significant results is likely to be less than 100%.
In fact, z-curve makes it possible to estimate conditional power of significant studies. First, z-curve estimates unconditional average power of significant studies. This parameter is called the expected replication rate (ERR) because it predicts how many studies would produce a significant result again in a hypothetical replication project that reproduces the original studies exactly with new samples. The ERR is 54% with an upper limit of 60% for the 95% confidence interval. We also know that no more than 20% of these studies are false positives. Assuming 80% true hypotheses, the average conditional power can not be higher than (.60 – .20*.05) / .8 = 74%. Thus, Soric’s assumption of 100% power is conservative, and the false positive rate is likely to be lower.
In conclusion, a z-curve analysis of Nord et al.’s power estimates for Button et al.’s meta-analyses confirms estimates that could have been obtained by applying Soric’s formula to Button et al.’s estimate of mean power. The true rate of false positive results remains unknown, but it is unlikely to be more than 20%.
Heterogeneity Across Research Areas
Nord et al. (2017) demonstrated that power varies across different research areas that were included in Button et al.’s sample of meta-analyses. Some of these areas had enough studies to conduct z-curve analyses for these specific areas. The most interesting area are candidate-gene studies that relate genotypic variation in single genes to phenotypes across participants With the benefit of hindsight, it is known that variation in a single gene has trivial effects on complex traits and that many of the significant results in these studies were practically false positive results (Duncan & Keller, 2011). 234 of the 730 studies were from this research area. Figure 3 shows the results. Interestingly, only 11% of the results were statistically significant. Thus, the low average power can be explained by many studies that reported non-significant results. There is no evidence of publication bias in these meta-analyses.
Using Soric’s formula, the low EDR translates into a high false positive risk, 42% and the upper limit of the 95% confidence interval includes 100%. Thus, z-curve confirms that the rare significant results in this literature could be false positive results. Most significant results also are just significant. There are hardly any results that show strong evidence (z > 4) against the null-hypothesis.
In short, a large portion of the 730 studies came from a research area that is known to have produced few significant results. This finding implies that other research areas are producing more credible significant results (Nord et al., 2017).
A second set of meta-analyses were clinical trials. Clinical trials have received considerable attention using Cochrane meta-analyses and abstracts in original articles that often report the key statistical result ( (Jager & Leek, 2013; Schimmack & Bartos, 2023, van Zwet et al., 2024). The results suggest that unconditional mean power is around 30% and the false positive risk is between 10% and 20%. These results serve as benchmarks for the z-curve analysis of the 145 clinical trials in Button et al.’s study (Figure 4).
The EDR is somewhat lower, 21%, but the 95% confidence interval includes 30%. The FDR is 19%, but the lower limit of the confidence interval includes 13%. Thus, the results are a bit lower, but mostly consistent with evidence from estimates based on thousands of results. These estimates of the FDR are notably lower than the false positive rates that were predicted by Ioannidis’s scenarios that assumed high rates of true null-hypotheses.
The third domain were studies from psychology. Psychological scientists have examined the credibility of their research in the wake of replication failures (Open Science Collaboration, 2015). Suddenly, only significant results in multiple studies within a single study were no longer attributed to reliable effects, but seen as signs of selection for significance (Schimmack, 2012). Francis (2014) found that over 80% of these multi-study articles showed statistically significant evidence of bias. Large scale multi-lab replication studies failed also showed that effect sizes estimates in these studies could be inflated by a factor of 1,000, shrinking effect sizes from d = .6 to d = .06 (Vohs et al., 2019). A z-curve analysis of a representative sample of studies in social psychology estimated that average unconditional power before selection for significance, EDR = 19%, FDR = 22%. Cohen (1962) already found similar estimates are similar for focal and non-focal results. This was also the case in a survey of emotion research (Soto & Schimmack, 2024). Soto and Schimmack (2024) reported an EDR of 30% and a corresponding FDR = 12% (k sig = 21,628) for all automatically extracted tests, and an EDR of 27%, FDR = 14%, for hand-coded focal tests (k sig = 227). These results serve as a comparison standard for the z-curve of 145 studies classified as psychological research by Nord et al. (2017). The EDR is 49%, FDR = 5%. Even the lower limit of the EDR confidence interval, 39%, implies only 8% false positives. among the significant results.
There are several reasons why these results differ from other findings. First, the focus on meta-analyses leads to an unrepresentative sample of the entire literature. Meta-analyses often include a lot more non-significant results and have less bias than original articles. Second, the specific set of meta-analyses was not representative of the broader literature in psychology. Thus, the results cannot be generalized from the specific studies in Button et al.’s sample to psychology or neuroscience. That would require representative sampling or collecting data from all studies using automatic extraction of test statistics.
Discussion
Button et al.’s (2013) was a first attempt to assess the credibility of empirical results with empirical estimates of power based on meta-analytic effect sizes and sample sizes. The median power was low (21%). The key implications of these finding was that researchers often fail to reject null-hypotheses and may use questionable research practices to report significant results in published articles. Low power and bias could lead to many false positive results. This article added to other concerns about the reliability of findings in neuroscience (Vul et al., 2019).
Most citations took Button et al.’s findings and implications at face value. Nord et al. (2017) pointed out that power and false positive rates varied across research areas. Most notably, candidate gene studies have lower power and a much higher false positive risk. Including these studies in the calculation of median power may have led to false perceptions of other research areas.
Here I presented the first serious critical examination of Button et al.’s methodology and inferences and found several problems that undermine their pessimistic assessment of neuroscience. First, they estimated unconditional power, but their false positive calculations require estimates of conditional power. Second, false positives rates depend on mean power and not median power. Mean power was 35% which is close to the estimate for psychology based on actual replication studies (OSC, 2015). Third, they made unnecessary assumptions about ratios of true and false hypotheses being tested, when unconditional power alone is sufficient to estimate false positive rates (Soric, 1989). Fourth, they relied on meta-analysis to correct for publication bias, but meta-analyses are not representative of the broader literature.
Meta-science is like other sciences. Ideally, critical analyses reveal problems and new innovations address these problems. Power estimation started in the 1960s with Cohen’s seminal article. Cohen (1962) worked with plausible effect sizes, but did not aim to estimate studies true power. Moreover, his work and statistical power were largely ignored (Cohen, 1990; Sedlmeier & Gigenzer, 1989).
Conclusion
The replication crisis stimulated renewed interest in methods that use observed results to draw inferences about the power of actual studies (Ioannidis & Trikalinos, 2007; Francis, 2014; Schimmack, 2012; Simonsohn, Nelson, & Simmons, 2014). This work shifted attention from prospective power calculations to the retrospective assessment of evidential strength in published literatures. Two challenges emerged as central. First, selection bias inflates the observed rate of significant results, requiring methods that correct for selection. Second, power varies across studies, requiring models that allow for heterogeneity rather than assuming a single common effect size or power level. Early approaches addressed selection under simplifying assumptions, typically treating power as homogeneous across studies. As a result, their inferences become unreliable when studies differ in sample size, effect size, or both (Brunner & Schimmack, 2020; Schimmack, 2026).
Z-curve extends this line of work by explicitly modeling both selection and heterogeneity, estimating a distribution of power across studies rather than a single average. This provides a framework for quantifying key properties of the literature, including expected discovery and replication rates, and for linking these quantities to false discovery risk (Sorić, 1989). In this sense, z-curve represents a substantive advance in the empirical assessment of the credibility of published findings. Like earlier contributions such as Button et al., it is unlikely to be the final word, but it is currently the most advanced method to estimate true power for sets of studies with heterogeneity in power and selection bias.
Full citation: Soto, M. D., & Schimmack, U. (2024). Credibility of results in emotion science: A Z-curve analysis of results in the journals Cognition & Emotion and Emotion. Cognition and Emotion. https://doi.org/10.1080/02699931.2024.2443016
Purpose of this document: This is a detailed analytical summary written entirely in the summarizer’s own words. It is intended to make the paper’s methods, results, and arguments accessible for discussion and analysis without reproducing copyrighted text. Readers should consult the original article for exact language and figures.
Structured Summary
1. Motivation and Research Question
The paper addresses whether the replication crisis — documented most prominently by the Open Science Collaboration (2015), which found only 36% of psychology results replicated — extends to the emotion research literature specifically. The authors note that the OSC findings were limited to articles from 2008 and may not generalize to emotion research, which has its own dedicated journals and traditions.
The two journals examined are Cognition & Emotion (established 1987) and Emotion (established 2001 by APA). The authors aimed to assess: (a) how much selection bias exists in these journals, (b) what proportion of published results might be false positives, (c) what the expected replication rate is, and (d) whether these indicators have improved over time in response to the replication crisis.
2. Z-Curve Method: How It Works
The paper uses Z-curve 2.0 (Bartoš & Schimmack, 2022), which takes a set of test statistics, converts them to absolute z-scores, and fits a finite mixture model to the distribution of statistically significant z-values (those exceeding 1.96). The method produces four key estimates:
Expected Discovery Rate (EDR): An estimate of the average true power of studies before selection for significance. This represents what proportion of all conducted tests (including unpublished ones) would be expected to reach significance. It is conceptually the mean power across the full population of tests.
Expected Replication Rate (ERR): An estimate of mean power after selection for significance — that is, among published significant results. Because significance selection favors higher-powered studies, ERR is always higher than EDR. The authors frame ERR as an optimistic upper bound on expected replication success.
Observed Discovery Rate (ODR): Simply the proportion of extracted test statistics that were statistically significant at p < .05. Comparing ODR to EDR quantifies selection bias: a large gap indicates that many non-significant results went unreported.
False Discovery Risk (FDR): Computed from the EDR using Soric’s (1989) formula, which gives the maximum proportion of significant results that could be false positives given a particular discovery rate.
The authors explicitly note that ERR overestimates actual replication success (comparing z-curve’s ERR for the OSC dataset to the actual 36% rate), and they recommend interpreting the true replication rate as falling somewhere between EDR and ERR, citing Sotola (2023) for empirical support.
3. Methods
3.1 Test Statistic Extraction
The authors collected the complete set of published articles from both journals (3,831 from C&E covering 1987–2023; 2,323 from Emotion covering 2001–2023). Using custom R code built on the pdftools package (Ooms, 2024), they automatically extracted reported test statistics: F-tests, t-tests, chi-square tests (with df between 1 and 6 only, to exclude SEM model-fit tests), z-tests, and 95% confidence intervals of odds ratios and regression coefficients.
Chi-square tests with df > 6 were excluded because these typically come from structural equation modeling, where rejecting the null indicates poor model fit rather than a substantive finding. Confidence intervals were excluded when reported alongside test statistics to avoid double-counting. Meta-analysis articles were excluded entirely.
The extraction code was designed to handle various notation formats across journals and was iteratively refined. However, the authors acknowledge that the automated process cannot extract statistics from tables or figures, and cannot distinguish between focal and non-focal hypothesis tests.
After exclusions (including test statistics with N < 30, since t-to-z conversion is unreliable at very low df), the final samples were 30,513 z-scores from 1,902 C&E articles and 35,457 z-scores from 1,953 Emotion articles. The majority were F-tests (62% C&E, 53% Emotion) and t-tests (26% C&E, 28% Emotion).
3.2 Statistical Analysis — The Clustering Approach
This is a critical methodological detail. The authors used the zcurve_clustered function with the “b” method. This method works by sampling a single test statistic from each article during model fitting, thereby addressing within-article dependence. This directly addresses concerns about independence violations that arise when multiple test statistics are extracted from the same paper.
The EM algorithm was applied to significant z-values between 1.96 and 6 (values above 6 are treated as having essentially 100% power). The fitted mixture model uses seven discrete components (z = 0 through 6), and the estimated weights are used to compute EDR and ERR. The model then extrapolates the full distribution to estimate what the non-significant portion would look like without selection.
3.3 Time Trend Analysis
Annual z-curve estimates were computed for each publication year and regressed on linear and quadratic predictors of year. The quadratic term tested whether improvements accelerated after 2011 (when the replication crisis became prominent).
3.4 Hand-Coded Focal Tests
To address the limitation that automatic extraction conflates focal and non-focal tests, the authors also present results from 241 hand-coded articles from 2010 and 2020, drawn from an ongoing project covering 30+ journals and 4,000+ studies (Schimmack, 2020). This sample contained 227 significant tests out of 241 total.
4. Results
4.1 Main Z-Curve Estimates
The two journals produced remarkably similar results:
Parameter
Cognition & Emotion
Emotion
ODR
71% [70%, 71%]
70% [70%, 70%]
EDR
30% [14%, 53%]
31% [15%, 53%]
ERR
66% [59%, 73%]
65% [59%, 71%]
FDR
12% [5%, 32%]
12% [5%, 30%]
The ODR-EDR gap (approximately 40 percentage points) provides clear evidence of selection bias in both journals, confirmed visually by a sharp drop in observed z-scores just below the significance threshold of 1.96.
The ERR of approximately 65% suggests that the majority of published significant results should replicate with the same sample size, though the authors stress this is an optimistic estimate. The FDR point estimate of 12% is comparable to medical clinical trial journals (14% per Schimmack & Bartoš, 2023) and substantially lower than the most pessimistic predictions (Ioannidis, 2005). However, the upper bound of the FDR confidence interval (~30%) is high enough to warrant concern.
4.2 Time Trends
Sample sizes (degrees of freedom): Both journals showed significant linear increases over time, with some acceleration (significant quadratic trends). Median within-group df increased from roughly 50 in the early years to over 100 in recent years for Emotion, and showed a particularly sharp increase in C&E’s most recent years.
ODR: Both journals showed significant linear decreases in ODR over time (approximately 0.45 percentage points per year), suggesting that non-significant results are being reported more frequently. However, the quadratic terms were non-significant, meaning this trend preceded the replication crisis rather than being a response to it.
EDR: Both journals showed significant increases in EDR over time, consistent with increasing sample sizes leading to higher power. The combination of decreasing ODR and increasing EDR indicates that selection bias has diminished, though it remains present.
ERR: Increased over time for both journals, with C&E showing a significant acceleration (quadratic trend) suggesting the replication crisis may have prompted improvements.
FDR: Decreased over time as a direct consequence of the increasing EDR.
4.3 Hand-Coded Focal Test Results
The 241 hand-coded focal tests from 2010 and 2020 yielded:
Parameter
Estimate
95% CI
ODR
94%
[91%, 97%]
EDR
27%
[10%, 67%]
ERR
65%
[53%, 75%]
FDR
14%
[3%, 50%]
The ODR for focal tests (94%) is substantially higher than the 70–71% from automatic extraction, confirming that automatic extraction captures many non-focal, non-significant tests that dilute the ODR. However, the EDR, ERR, and FDR estimates are comparable to the automatically extracted results and fall within their confidence intervals. This is an important robustness check: the key z-curve parameters are not substantially altered by the inclusion of non-focal tests.
4.4 Alpha Adjustment Analysis
The authors examined the effect of lowering the significance threshold on discovery rates and false positive risk. Lowering alpha from .05 to .01 retains approximately half of all significant results while reducing FDR to below 5% for most publication years. Further reductions to .005 or .001 have diminishing returns for FDR reduction but increasingly sacrifice power.
5. Discussion and Interpretation
The authors frame their results as relatively encouraging for emotion research compared to worst-case scenarios. Key interpretive points:
The FDR of approximately 12% (though with wide CIs) suggests that most published significant results in emotion journals are not false positives. However, the upper bound of the CI leaves open the possibility of rates up to 30%.
The ERR of 65% predicts that most significant results should replicate with the same sample size, but this is optimistic. Adjusting for the estimated FDR, power for true effects may be approximately 72%, close to the conventional 80% benchmark but with substantial heterogeneity — half of studies have less power than this average.
The authors recommend treating results with p-values between .05 and .01 with skepticism, and suggest that alpha = .01 provides a better balance between false positive risk and power loss for the emotion literature specifically. They emphasize this recommendation is for evaluating existing literature, not as a new publication standard.
On effect sizes, the authors warn that selection bias inflates point estimates, making even meta-analytic effect sizes unreliable unless bias correction is applied. They advocate for honest reporting of all results, including non-significant ones, as essential for accurate meta-analysis.
6. Limitations Acknowledged by the Authors
The authors explicitly discuss several limitations:
Z-curve’s selection model assumes that publication probability is a function of power. In reality, questionable research practices (QRPs) can produce significance without real effects, potentially inflating EDR estimates and underestimating selection bias.
Simulation studies of z-curve performance under QRP-generated data are lacking.
The N > 30 exclusion removes some studies, though supplementary analyses with the full sample show similar results.
Automated extraction cannot distinguish focal from non-focal tests (addressed by the hand-coded analysis).
The automated extraction cannot reliably capture statistics from tables or figures.
7. Key Methodological Features Relevant to the Pek et al. Debate
Several aspects of this paper are directly relevant to criticisms raised by Pek et al.:
Independence assumption: Soto & Schimmack explicitly used zcurve_clustered with the “b” method, which samples one test statistic per article during bootstrapping. This directly addresses the concern about within-article dependence. The method section states this clearly.
Focal vs. non-focal tests: The paper includes both automatic extraction (all tests) and hand-coded focal tests, and shows that the z-curve parameters (EDR, ERR, FDR) are comparable across both approaches. This addresses the concern that including non-focal tests distorts results.
Appropriate caveats: The authors consistently describe ERR as optimistic, characterize the true replication rate as lying between EDR and ERR, acknowledge the wide confidence intervals on EDR and FDR, and explicitly discuss the limitations of the selection model assumption.
Asymmetric interpretation: The paper notes that z-curve evaluations of credibility are asymmetric — low values raise concerns about a literature, but high values do not guarantee credibility.
8. Summary Table of All Z-Curve Estimates
Analysis
N tests
N sig
ODR
EDR [95% CI]
ERR [95% CI]
FDR [95% CI]
C&E (auto)
30,513
21,628
71%
30% [14%, 53%]
66% [59%, 73%]
12% [5%, 32%]
Emotion (auto)
35,457
24,824
70%
31% [15%, 53%]
65% [59%, 71%]
12% [5%, 30%]
Focal (hand-coded)
241
227
94%
27% [10%, 67%]
65% [53%, 75%]
14% [3%, 50%]
Summary prepared for analytical discussion purposes. All descriptions reflect the summarizer’s interpretation of the original work. For exact language, figures, and supplementary analyses, consult the published article.
The pattern is now familiar. I received another anonymous review by Reviewer 2 from a z-curve article that repeated Pek’s concerns about the performance of z-curve. To deal with biased reviewers, journals allow authors to mention potentially biased reviewers. I suggest doing so for Pek. I also suggest sharing a manuscript with me to ensure proper interpretation of results and to make it “reviewer-safe.”
To justify the claim that Pek is biased, researchers can use this rebuttal of Pek’s unscientific claims about z-curve.
Reviewer 2
Reviewer Report:
The manuscript “A review and z-curve analysis of research on the palliative association of system justification” (Manuscript ID 1598066) extends the work of Sotola and Credé (2022), who used Z-curve analysis to evaluate the evidential value of findings related to system justification theory (SJT). The present paper similarly reports estimates of publication bias, questionable research practices (QRPs), and replication rates in the SJT literature using Z-curve. Evaluating how scientific evidence accumulates in the published literature is unquestionably important.
However, there is growing concern about the performance of meta-analytic forensic tools such as p-curve (Simonsohn, Nelson, & Simmons, 2014; see Morey & Davis-Stober, 2025 for a critique) and Z-curve (Brunner & Schimmack, 2020; Bartoš & Schimmack, 2022; see Pek et al., in press for a critique). Independent simulation studies increasingly suggest that these methods may perform poorly under realistic conditions, potentially yielding misleading results.
Justification for a theory or method typically requires subjecting it to a severe test (Mayo, 2019) – that is, assuming the opposite of what one seeks to establish (e.g., a null hypothesis of no effect) and demonstrating that this assumption leads to contradiction. In contrast, the simulation work used to support Z-curve (Brunner & Schimmack, 2020; Bartoš & Schimmack, 2022) relies on affirming belief through confirmation, a well-documented cognitive bias.
Findings from Pek et al. (in press) show that when selection bias is presented in published p-values — the very scenario Z-curve was intended to be applied — estimates of the expected discovery rate (EDR), expected replication rate (ERR), and Sorić’s False Discovery Risk (FDR) are themselves biased.
The magnitude and direction of this bias depend on multiple factors (e.g., number of p-values, selection mechanism of p-values) and cannot be corrected or detected from empirical data alone. The manuscript’s main contribution rests on the assumption that Z-curve yields reasonable estimates of the “reliability of published studies,” operationalized as a high ERR, and that the difference between the observed discovery rate (ODR) and EDR quantifies the extent of QRPs and publication bias.
The paper reports an ERR of .76, 95% CI [.53, .91] and concludes that research on the palliative hypothesis may be more reliable than findings in many other areas of psychology. There are several issues with this claim. First, the assertion that Sotola (2023) validated ERR estimates from the Z-curve reflects confirmation bias – I have not read Röseler (2023) and cannot comment on the argument made in it. The argument rests solely on the descriptive similarly between the ERR produced by Z-curve and the replication rate reported by the Open Science Collaboration (2015). However, no formal test of equivalence was conducted, and no consideration was given to estimate imprecision, potential bias in the estimates, or the conditions under which such agreement might occur by chance.
At minimum, if Z-curve estimates are treated as predicted values, some form of cross-validation or prediction interval should be used to quantify prediction uncertainty. More broadly, because ERR estimates produced by Z-curve are themselves likely biased (as shown in Pek et al., in press), and because the magnitude and direction of this bias are unknown, comparisons about ERR values across literatures do not provide a strong evidential basis for claims about the relative reliability of research areas.
Furthermore, the width of the 95% CI spans roughly half of the bounded parameter space of [0, 1], indicating substantial imprecision. Any claims based on these estimates should thus be contextualized with appropriate caution.
Another key result concerns the comparison of EDR = .52, 95% CO [.14, .92], and ODR = .81, 95% CI = [.69, .90]. The manuscript states that “When these two estimates are highly discrepant, this is consistent with the presence of questionable research practices (QRPS) and publication bias in this area of research (Brunner & Schimmack, 2020).
But in this case, the 95% CIs for the EDR and ODR in this work overlapped quite a bit, meaning that they may not be significantly different…” (p. 22). There are several issues with such a claim. First, Z curve results cannot directly support claims about the presence of QRPs.
The EDR reflects the proportion of significant p values expected under no selection bias, but it does not identify the source of selection bias (e.g., QRPs, fraud, editorial decisions). Using Z curve requires accepting its assumed missing data mechanism—a strong assumption that cannot be empirically validated.
Second, a descriptive comparison between two estimates cannot be interpreted as a formal test of difference (e.g., eyeballing two estimates of means as different does not tell us whether this difference is not driven by sampling variability). Means can be significantly different even if their confidence intervals overlap (Cumming & Finch, 2005).
A formal test of the difference is required. Third, EDR estimates can be biased. Even under ideal conditions, convergence to the population values requires extremely large numbers of studies (e.g., > 3000, see Figure 1 of Pek et al., in press).
The current study only has 64 tests. Thus, even if a formal test of the difference of ODR – EDR was conducted, little confidence could be placed on the result if the EDR estimate is biased and does not reflect the true population value.
Although I am critical of the outputs of Z curve analysis due to its poor statistical performance under realistic conditions, the manuscript has several strengths. These include adherence to good meta analytic practices such as providing a PRISMA flow chart, clearly stating inclusion and exclusion criteria, and verifying the calculation of p values. These aspects could be further strengthened by reporting test–retest reliability (given that a single author coded all studies) and by explicitly defining the population of selected p values. Because there appears to be heterogeneity in the results, a random effects meta analysis may be appropriate, and study level variables (e.g., type of hypothesis or analysis) could be used to explain between study variability. Additionally, the independence of p values has not been clearly addressed; p values may be correlated within articles or across studies. Minor points: The “reliability” of studies should be explicitly defined. The work by Manapat et al. (2022) should be cited in relation to Nagy et al. (2025). The findings of Simmons et al. (2011) applies only to single studies.
However, most research is published in multi-study sets, and follow-up simulations by Wegener at al. (2024) indicate that the Type I error rate is well-controlled when methodological constraints (e.g., same test, same design, same measures) are applied consistently across multiple studies – thus, the concerns of Simmons et al. (2011) pertain to a very small number of published results.
I could not find the reference to Schimmack and Brunner (2023) cited on p. 17.
Rebuttal to Core Claims in Recent Critiques of z-Curve
1. Claim: z-curve “performs poorly under realistic conditions”
Rebuttal
The claim that z-curve “performs poorly under realistic conditions” is not supported by the full body of available evidence. While recent critiques demonstrate that z-curve estimates—particularly EDR—can be biased under specific data-generating and selection mechanisms, these findings do not justify a general conclusion of poor performance.
Z-curve has been evaluated in extensive simulation studies that examined a wide range of empirically plausible scenarios, including heterogeneous power distributions, mixtures of low- and high-powered studies, varying false-positive rates, different degrees of selection for significance, and multiple shapes of observed z-value distributions (e.g., unimodal, right-skewed, and multimodal distributions). These simulations explicitly included sample sizes as low as k ≈ 100, which is typical for applied meta-research in psychology.
Across these conditions, z-curve demonstrated reasonable statistical properties conditional on its assumptions, including interpretable ERR and EDR estimates and confidence intervals with acceptable coverage in most realistic regimes. Importantly, these studies also identified conditions under which estimation becomes less informative—such as when the observed z-value distribution provides little information about missing nonsignificant results—thereby documenting diagnosable scope limits rather than undifferentiated poor performance.
Recent critiques rely primarily on selective adversarial scenarios and extrapolate from these to broad claims about “realistic conditions,” while not engaging with the earlier simulation literature that systematically evaluated z-curve across a much broader parameter space. A balanced scientific assessment therefore supports a more limited conclusion: z-curve has identifiable limitations and scope conditions, but existing simulation evidence does not support the claim that it generally performs poorly under realistic conditions.
2. Claim: Bias in EDR or ERR renders these estimates uninterpretable or misleading
Rebuttal
The critique conflates the possibility of bias with a lack of inferential value. All methods used to evaluate published literatures under selection—including effect-size meta-analysis, selection models, and Bayesian hierarchical approaches—are biased under some violations of their assumptions. The existence of bias therefore does not imply that an estimator is uninformative.
Z-curve explicitly reports uncertainty through bootstrap confidence intervals, which quantify sampling variability and model uncertainty given the observed data. No evidence is presented that z-curve confidence intervals systematically fail to achieve nominal coverage under conditions relevant to applied analyses. The appropriate conclusion is that z-curve estimates must be interpreted conditionally and cautiously, not that they lack statistical meaning.
This claim overgeneralizes results from specific, highly constrained simulation scenarios. The cited sample sizes correspond to conditions in which the observed data provide little identifying information, not to a general requirement for statistical validity.
In applied statistics, consistency in the limit does not imply that estimates at smaller sample sizes are meaningless; it implies that uncertainty must be acknowledged. In the present application, this uncertainty is explicitly reflected in wide confidence intervals. Small sample sizes therefore affect precision, not validity, and do not justify dismissing the estimates outright.
4. Claim: Differences between ODR and EDR cannot support inferences about selection or questionable research practices
Rebuttal
It is correct that differences between ODR and EDR do not identify the source of selection (e.g., QRPs, editorial decisions, or other mechanisms). However, the critique goes further by implying that such differences lack diagnostic value altogether.
Under the z-curve framework, ODR–EDR discrepancies are interpreted as evidence of selection, not of specific researcher behaviors. This inference is explicitly conditional and does not rely on attributing intent or mechanism. Rejecting this interpretation would require demonstrating that ODR–EDR differences are uninformative even under monotonic selection on statistical significance, which has not been shown.
5. Claim: ERR comparisons across literatures lack evidential basis because bias direction is unknown
Rebuttal
The critique asserts that because ERR estimates may be biased with unknown direction, comparisons across literatures lack evidential value. This conclusion does not follow.
Bias does not eliminate comparative information unless it is shown to be large, variable, and systematically distorting rankings across plausible conditions. No evidence is provided that ERR estimates reverse ordering across literatures or are less informative than alternative metrics. While comparative claims should be interpreted cautiously, caution does not imply the absence of evidential content.
6. Claim: z-curve validation relies on “affirming belief through confirmation”
Rebuttal
This characterization misrepresents the role of simulation studies in statistical methodology. Simulation-based evaluation of estimators under known data-generating processes is the standard approach for assessing bias, variance, and coverage across frequentist and Bayesian methods alike.
Characterizing simulation-based validation as epistemically deficient would apply equally to conventional meta-analysis, selection models, and hierarchical Bayesian approaches. No alternative validation framework is proposed that would avoid reliance on model-based simulation.
7. Implicit claim: Effect-size meta-analysis provides a firmer basis for credibility assessment
Rebuttal
Effect-size meta-analysis addresses a different inferential target. It presupposes that studies estimate commensurable effects of a common hypothesis. In heterogeneous literatures, pooled effect sizes represent averages over substantively distinct estimands and may lack clear interpretation.
Moreover, effect-size meta-analysis does not estimate discovery rates, replication probabilities, or false-positive risk, nor does it model selection unless explicitly extended. No evidence is provided that effect-size meta-analysis offers superior performance for evaluating evidential credibility under selective reporting.
Summary
The critiques correctly identify that z-curve is a model-based method with assumptions and scope conditions. However, they systematically extend these points beyond what the evidence supports by:
extrapolating from selective adversarial simulations,
conflating potential bias with lack of inferential value,
overgeneralizing small-sample limitations,
and applying asymmetrical standards relative to conventional methods.
A scientifically justified conclusion is that z-curve provides conditionally informative estimates with quantifiable uncertainty, not that it lacks statistical validity or evidential relevance.
In the 17th century, early telescopic observations of Mars suggested that the planet might be populated. Now imagine a study that aims to examine whether Martians are taller than humans. The problem is obvious: although we may assume that Martians exist, we cannot observe or measure them, and therefore we end up with zero observations of Martian height. Would we blame the t-test for not telling us what we want to know? I hope your answer to this rhetorical question is “No, of course not.”
If you pass this sanity check, the rest of this post should be easy to follow. It responds to criticism by Erik van Zwet (EvZ), hosted and endorsed by Andrew Gelman on his blog,
EvZ imagines a scenario in which z-curve is applied to data generated by two distinct lines of research. One lab conducts studies that test only true null hypotheses. While exact effect sizes of zero may be rare in practice, attempting to detect extremely small effects in small samples is, for all practical purposes, equivalent. A well-known example comes from early molecular genetic research that attempted to link variation in single genes—such as the serotonin transporter gene—to complex phenotypes like Neuroticism. It is now well established that these candidate-gene studies produced primarily false positive results when evaluated with the conventional significance threshold of α = .05.
In response, molecular genetics fundamentally changed its approach. Researchers began testing many genetic variants simultaneously and adopted much more stringent significance thresholds to control the multiple-comparison problem. In the simplified example used here, I assume α = .001, implying an expected false positive rate of only 1 in 1,000 tests. I further assume that truly associated genetic predictors—single nucleotide polymorphisms (SNPs)—are tested in very large samples, such that sampling error is small and true effects yield z-values around 6. This is, of course, a stylized assumption, but it serves to illustrate the logic of the critique.
Figure 1 illustrates a situation with 1,000 studies from each of these two research traditions. Among the 1,000 candidate-gene studies, only one significant result is expected by chance. Among the genome-wide association studies (GWAS), power to reject the null hypothesis at α = .001 is close to 1, although a small number (3–4 out of 1,000) of studies may still fail to reach significance.
At this point, it is essential to distinguish between two scenarios. In the first scenario, all 999 non-significant results are observed and available for analysis. If we could recover the full distribution of results—including non-significant ones—we could fit models to the complete set of z-values. Z-curve can, in principle, be applied to such data, but it was not designed for this purpose.
Z-curve was developed for the second scenario. In this scenario, the light-purple, non-significant results exist only in researchers’ file drawers and are not part of the observed record. This situation—selection for statistical significance—is commonly referred to as publication bias. In psychology, success rates above 90% strongly suggest that statistical significance is a necessary condition for publication (Sterling, 1959). Under such selection, non-significant results provide no observable information, and only significant results remain. In extreme cases, it is theoretically possible that all published significant findings are false positives (Rosenthal, 1979), and in some literatures—such as candidate-gene research or social priming—this possibility is not merely theoretical.
Z-curve addresses uncertainty about the credibility of published significant results by explicitly conditioning on selection for significance and modeling only those results. When success rates approach 90% or higher, there is often no alternative: non-significant results are simply unavailable.
In Figure 1, the light-purple bars represent non-significant results that exist only in file drawers. Z-curve is fitted exclusively to the dark-purple, significant results. Based on these data, the fitted model (red curve), which is centered near the true value of z = 6, correctly infers that the average true power of the studies contributing to the significant results is approximately 99% when α = .001 (corresponding to a critical value of z ≈ 3.3).
Z-curve also estimates the Expected Discovery Rate (EDR). Importantly, the EDR refers to the average power of all studies that were conducted in the process of producing the observed significant results. This conditioning is crucial. Z-curve does not attempt to estimate the total number of studies ever conducted, nor does it attempt to account for studies from populations that could not have produced the observed significant findings. In this example, candidate-gene studies that produced non-significant results—whether published or not—are irrelevant because they did not contribute to the set of significant GWAS results under analysis.
What matters instead is how many GWAS studies failed to reach significance and therefore remain unobserved. Given the assumed power, this number is at most 3–4 out of 1,000 (<1%). Consequently, an EDR estimate of 99% is correct and indicates that publication bias within the relevant population of studies is trivial. Because the false discovery rate is derived from the EDR, the implied false positive risk is effectively zero—again, correctly so for this population.
EvZ’s criticism of z-curve is therefore based on a misunderstanding of the method’s purpose and estimand. He evaluates z-curve against a target that includes large numbers of studies that leave no trace in the observed record and have no influence on the distribution of significant results being analyzed. But no method that conditions on observed significant results can recover information about such studies—nor should it be expected to.
Z-curve is concerned exclusively with the credibility of published significant results. Non-significant studies that originate from populations that do not contribute to those results are as irrelevant to this task as the height of Martians.
Bartoš, F., & Schimmack, U. (2022). Z-curve 2.0: Estimating replication rates and discovery rates. Meta-Psychology, 6, Article e0000130. https://doi.org/10.15626/MP.2022.2981
Brunner, J., & Schimmack, U. (2020). Estimating population mean power under conditions of heterogeneity and selection for significance. Meta- Psychology. MP.2018.874, https://doi.org/10.15626/MP.2018.874
van Zwet, E., Gelman, A., Greenland, S., Imbens, G., Schwab, S., & Goodman, S. N. (2024). A New Look at P Values for Randomized Clinical Trials. NEJM evidence, 3(1), EVIDoa2300003. https://doi.org/10.1056/EVIDoa2300003
The Story of Two Z-Curve Models
Erik van Zwet recently posted a critique of the z-curve method on Andrew Gelman’s blog.
Meaningful discussion of the severity and scope of this critique was difficult in that forum, so I address the issue more carefully here.
van Zwet identified a situation in which z-curve can overestimate the Expected Discovery Rate (EDR) when it is inferred from the distribution of statistically significant z-values. Specifically, when the distribution of significant results is driven primarily by studies with high power, the observed distribution contains little information about the distribution of nonsignificant results. If those nonsignificant results are not reported and z-curve is nevertheless used to infer them from the significant results alone, the method can underestimate the number of missing nonsignificant studies and, as a consequence, overestimate the Expected Discovery Rate (EDR).
This is a genuine limitation, but it is a conditional and diagnosable one. Crucially, the problematic scenarios are directly observable in the data. Problematic data have an increasing or flat slope of the significant z-value distribution and a mode well above the significance threshold. In such cases, z-curve does not silently fail; it signals that inference about missing studies is weak and that EDR estimates should not be trusted.
This is rarely a problem in psychology, where most studies have low power, the mode is at the significance criterion, and the slope decreases, often steeply. This pattern implies a large set of non-significant results and z-curve provides good estimates in these scenarios. It is difficult to estimate distributions of unobserved data, leading to wide confidence intervals around these estimates. However, there is no fixed number of studies that are needed. The relevant question is whether the confidence intervals are informative enough to support meaningful conclusions.
One of the most powerful set of studies that I have actually seen comes from epidemiology, where studies often have large samples to estimate effect sizes precisely. In these studies, power to reject the null hypothesis is actually not really important, but the data serve as a good example of a set of studies with high power, rather than low power as in psychology.
However, even this example shows a decreasing slope and a mode at significance criterion. Fitting z-curve to these data still suggests some selection bias and no underestimation of reported non-significant results. This illustrates how extreme van Zwet’s scenario must be to produce the increasing-slope pattern that undermines EDR estimation.
What about van Zwet’s Z-Curve Method?
It is also noteworthy that van Zwet does not compare our z-curve method (Bartos & Schimmack, 2022; Brunner & Bartos, 2020) to his own z-curve method that was used to analyze z-values from clinical trials (van Zwet et al., 2024).
The article fits a model to the distribution of absolute z-values (ignoring whether results show a benefit or harm to patients). The key differences between the two approaches are that (a) van Zwet et al.’s model uses all z-values and assumes (implicitly) that there is no selection bias, and (b) that true effect sizes are never zero and errors can only be sign errors. Based on these assumptions, the article concludes that no more than 2% of clinical trials produce a result that falsely rejects a true hypothesis. For example, a statistically significant result could be treated as an error only if the true effect has the opposite sign (e.g., the true effect increases smoking, but a significant result is used to claim it reduced smoking).
The advantage of this method is that it is not necessary to estimate the EDR from the distribution of only significant results, but it does so only by assuming that publication bias does not exist. In this case, we can just count the observed non-significant and significant results and use the observed discovery rate to estimate average power and the false positive risk.
The trade-off is clear. z-curve attempts to address selection bias and sometimes lacks sufficient information to do so reliably; van Zwet’s approach achieves stable estimates by assuming the problem away. The former risks imprecision when information is weak; the latter risks bias when its core assumption is violated.
In the example from epidemiology, there is evidence of some publication bias and omission of non-significant results. Using van Zwet’s model would be inappropriate because it would overestimate the true discovery rate. The focus on sign errors alone is also questionable and should be clearly stated as a strong assumption. It implies that significant results in the right direction are not errors, even if effect sizes are close to zero. For example, a significant result that suggests it extends life is considered a true finding, even if the effect size is one day.
False positive rates do not fully solve that problem, but false positive rates that include zero as a hypothetical value for the population effect size are higher and treat small effects close to zero as errors rather than treating half of them as correct rejections of the null hypothesis. For example, an intervention that decreases smoking by 1% of all smokers is not really different from one that increases it by 1%, but a focus on signs treats only the latter one as an error.
In short, van Zwet’s critique identifies a boundary condition for z-curve, not a general failure. At the same time, his own method rests on a stronger and untested assumption—no selection bias—whose violation would invalidate its conclusions entirely. No method is perfect and using a single scenario to imply that a method is always wrong is not a valid argument against any method. By the same logic, van Zwet’s own method could be declared “useless” whenever selection bias exists, which is precisely the point: all methods have scope conditions.
Using proper logic, we suggest that all methods work when assumptions are met. The main point is to test whether they are met or not. We clarified that z-curve estimation of the EDR assumes that enough low powered studies produced significant results to influence the distribution of significant results. If the slope of significant results is not decreasing, this assumption does not hold and z-curve should not be used to estimate the EDR. Similarly, users of van Zwets first method should first test whether selection bias is present and not use it when it does. They should also examine whether they think a proportion of studies could have tested practically true null hypotheses and not use the method when this is a concern.
Finally, the blog post responds to Gelman’s polemic about our z-curve method and earlier work by Jager and Leek (2014), by noting that Gelman’s critic of other methods exist in parallel to his own work (at least co-authorship) that also modeled distribution of z-values to make claims about power and the risk of false inferences. The assumption of this model that selection bias does not exist is peculiar, given Gelman’s typical writing about low power and the negative effects of selection for significance. A more constructive discussion would apply the same critical standards to all methods—including one’s own.
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1. Has z-curve been tested with simulation studies?
Yes. The original z-curve method was evaluated in large-scale simulation studies by Jerry Brunner. The extended z-curve 2.0 was tested by Frantisek Bartoš. The results of these simulation studies were part of the manuscripts submitted for publication. They have also been reproduced by independent researchers. The results and the code to reproduce or run new analyses are shared on the Open Science Framework.
It is important to distinguish between estimation of the Expected Replication Rate (ERR) and the Expected Discovery Rate (EDR). The ERR estimates the average true power of the significant results. It is estimated with high accuracy even with fewer than 50 studies. The EDR predicts the distribution of non-significant results that were not observed. This prediction is more difficult and requires more information from the significant results. With small samples, confidence intervals are naturally wide, but their width is data-dependent and informative in itself.
In short, ERR estimates can be obtained even with small sets of significant results. They are also preferable to p-curve’s estimates of average power, which degrade when studies vary in power. EDR estimates are trustworthy with more than 50 significant results.
Does z-curve fail when power is homogeneous and falls between grid points?
The discrete mixture model uses fixed components at noncentrality parameters 0 through 6. When all studies share a single noncentrality that falls between two grid points — for example, NCP = 1.5 — the model must approximate a point mass using weights on flanking components. Van Zwet (2026) showed that this maximizes approximation error and can bias the EDR estimate.
Z-curve 3.0 addresses this directly. When low heterogeneity is detected, the algorithm fits a single-component model with a free noncentrality parameter and adds the estimated NCP as an additional component. The EM algorithm then places weight on this data-driven component rather than splitting weight awkwardly across the fixed grid. In simulations with NCP = 1.5, the added component recovers the correct location and the bias disappears.
When power varies across studies — as in any real meta-analysis of conceptual replications — the discrete model performs well without this correction. The mixture weights approximate the underlying distribution of power much like a histogram approximates a smooth density. Simulation studies confirm that the discrete model outperforms a parametric normal model under high heterogeneity, because it makes no assumption about the shape of the power distribution. In this sense, the discrete model is better understood as a distribution-free (nonparametric) estimator, and its flexibility is an advantage rather than a limitation.
3. Does z-curve offer options for small sample (small-N) literatures like animal research?
Short answer: Yes — z-curve 3.0 adds new transformation methods and a t-curve option that make the method more appropriate for analyses involving small samples (e.g., N < 30). These options are designed to mitigate biases that arise when you convert small-sample test statistics to z-scores using standard normal approximations. Z-curve.3.0 also allows researchers to use t-distributions (t-curve) with a fixed df that is more similar to the distributions of test statistics from small samples than the standard normal distribution.
Details:
The z-curve 3.0 tutorial (Chapter 8) explains that instead of only converting p-values to z-scores, you can now:
Try alternative transformations of t-values that better reflect their sampling distribution, and
Use a direct t-curve model that fits t-distributions with specified degrees of freedom instead of forcing a normal approximation. This “t-curve” option is recommended when studies have similar and genuinely small degrees of freedom (like many animal experiments). (replicationindex.com)
These improvements help reduce bias introduced by naïve normal transformations, though they don’t completely eliminate all small-sample challenges, and performance can still be unstable when degrees of freedom vary widely or are extremely small. (replicationindex.com)
This is the final version of our response to Pek et al.’s criticism of z-curve in Cognition and Emotion that is now accepted for publication. I share it here as the actual response is hidden behind a paywall. To cite this content, use the following official citation:
Schimmack, U., & Soto, M. D. (2026). A response to Pek et al.’s commentary on Z-curve: clarifying the assumptions of selection models. Cognition and Emotion, 1–5. https://doi.org/10.1080/02699931.2026.2678998
Abstract
Pek et al. (2026) comment on Soto and Schimmack (2025) and raise concerns about the use of z-curve to evaluate the credibility of emotion research. Their central criticism is based on simulations showing that z-curve can overestimate the expected discovery rate when selection operates not only at the level of statistical significance but also within the set of significant results as a function of effect size. This point is correct: if researchers selectively publish larger significant effects while suppressing smaller significant ones, selection models that assume threshold-based filtering can be biased. However, this limitation is not unique to z-curve and applies equally to other selection models used in meta-analysis. More importantly, there is currently little empirical evidence for effect-size bias, while there is ample evidence of selection based on significance. Under these more realistic conditions, z-curve provides informative estimates of (a) selection bias, (b) the expected replication rate, and (c) the false positive risk. Our results also demonstrate substantial inflation of effect size estimates in traditional meta-analyses that ignore selection processes. For these reasons, we reject the recommendation to rely solely on standard meta-analytic approaches and advocate for the use of selection models to obtain more realistic estimates.
Chapter 6 uses the simulation from Chapter 4 to compare the performance of the default z-curve method with a z-curve that assumes a normal distribution of population effect sizes. The simulation highlights the problem of making distribution assumptions. One of the strengths of z-curve is that it does not make an assumption about the distribution of power. zcurve3.0/Tutorial.R.Script.Chapter6.R at main · UlrichSchimmack/zcurve3.0
Chapter 7 uses the simulation from Chapter 4 to compare the performance of z-curve to a Bayesian mixture model (bacon). The aim of bacon is different, but it also fits a mixture model to a set of z-values. The simulation results show that z-curve performs better than the Bayesian mixture model. zcurve3.0/Tutorial.R.Script.Chapter7.R at main · UlrichSchimmack/zcurve3.0
Chapter 8 uses the simulation from Chapter 4 to examine the performance of z-curve with t-values from small studies (N = 30). It introduces a new transformation method that performs better than the default method from z-curve.2.0 and it introduces the t-curve option to analyze t-values from small studies with t-distributions. zcurve3.0/Tutorial.R.Script.Chapter8.R at main · UlrichSchimmack/zcurve3.0
Chapter 9 simulates p-hacking by combining small samples with favorable trends into a larger sample with a significant result (patchwork samples). The simulation simulates studies with between-subject two-group designs with varying means and SD of effect sizes and sample sizes. It also examines the ability of z-curve to detect p-hacking and compares the performance of the default z-curve that does not make assumptions about the distribution of power and a z-curve model that assumes a normal distribution of power. zcurve3.0/Tutorial.R.Script.Chapter9.R at main · UlrichSchimmack/zcurve3.0
Brief ChatGPT Generated Summary of Key Points
What Is Z-Curve?
Z-curve is a statistical tool used in meta-analysis, especially for large sets of studies (e.g., more than 100). It can also be used with smaller sets (as few as 10 significant results), but the estimates become less precise.
There are several types of meta-analysis:
Direct replication: Studies that test the same hypothesis with the same methods. Example: Several studies testing whether aspirin lowers blood pressure.
Conceptual replication: Studies that test a similar hypothesis using different procedures or measures. Example: Different studies exploring how stress affects memory using different tasks and memory measures.
In direct replications, we expect low variability in the true effect sizes. In conceptual replications, variability is higher due to different designs.
Z-curve was primarily developed for a third type of meta-analysis: reviewing many studies that ask different questions but share a common feature—like being published in the same journal or during the same time period. In these cases, estimating an average effect size isn’t very meaningful because effects vary so much. Instead, z-curve focuses on statistical integrity, especially the concept of statistical power.
What Is Statistical Power?
I define statistical power as the probability that a study will produce a statistically significant result (usually p < .05).
To understand this, we need to review null hypothesis significance testing (NHST):
Researchers test a hypothesis (like exercise increasing lifespan) by conducting a study.
They calculate the effect size (e.g., exercise increase the average lifespan by 2 years) and divide it by the standard error to get a test statistic (e.g., a z-score).
Higher test-statistics imply a lower probability that the null hypothesis is true. The null hypothesis is that there is no effect. If the probability is below the conventional criterion of 5%, the finding is interpreted as evidence of an effect.
Power is the probability of obtaining a significant result, p < .05.
Hypothetical vs. Observed Power
Textbooks often describe power in hypothetical terms. For example, before collecting data, a researcher might assume an effect size and calculate how many participants are needed for 80% power.
But z-curve does something different. It estimates the average true power of a set of studies. It is only possible to estimate average true power for sets of studies because power estimates based on a single study are typically too imprecise to be useful. Z-curve provides estimates of the average true power of a set of studies and the uncertainty in these estimates.
Populations of Studies
Brunner and Schimmack (2020) introduced an important distinction:
All studies ever conducted (regardless of whether results were published).
Only published studies, which are often biased toward significant results.
If we had access to all studies, we could simply calculate power by looking at the proportion of significant results. For example, if 50% of all studies show p < .05, then the average power is 50%.
In reality, we only see a biased sample—mostly significant results that made it into journals. This is called selection bias (or publication bias), and it can mislead us.
What Z-Curve Does
Z-curve helps us correct for this bias by:
Using the p-values from published studies.
Converting them to z-scores (e.g., p = .05 → z ≈ 1.96).
Modeling the distribution of these z-scores to estimate:
The power of the studies we see,
The likely number of missing studies,
And the amount of bias.
Key Terms in Z-Curve
Term
Meaning
ODR (Observed Discovery Rate)
% of studies that report significant results
EDR (Expected Discovery Rate)
Estimated % of significant results we’d expect if there were no selection bias
ERR (Expected Replication Rate)
Estimated % of significant studies that would replicate if repeated exactly
FDR (False Discovery Rate)
Estimated % of significant results that are false positives
Understanding the Z-Curve Plot
Figure 1. Histogram of z-scores from 1,984 significant tests. The solid red line shows the model’s estimated distribution of observed z-values. The dashed line shows what we’d expect without selection bias. The Observed Discovery Rate (ODR) is 100%, meaning all studies shown are significant. However, the Expected Discovery Rate (EDR) is only 40%, suggesting many non-significant results were omitted. The Expected Replication Rate (ERR) is also 40%, indicating that only 40% of these significant results would likely replicate. The False Discovery Rate (FDR) is estimated at 8%.
Notice how the histogram spikes just above z = 2 (i.e., just significant) and drops off below. This pattern signals selection for significance, which is unlikely to occur due to chance alone.
Homogeneity vs. Heterogeneity of Power
Sometimes all studies in a set have similar power (called homogeneity). In that case, the power of significant and non-significant studies is similar.
However, z-curve allows for heterogeneity, where studies have different power levels. This flexibility makes it better suited to real-world data than methods that assume all studies are equally powered.
When power varies, high-power studies are more likely to produce significant results. That’s why, under heterogeneity, the ERR (for significant studies) is often higher than the EDR (for all studies).
Summary of Key Concepts
Meta-analysis = Statistical summary of multiple studies.
Statistical significance = p < .05.
Power = Probability of finding a significant result.
Selection bias = Overrepresentation of significant results in the literature.
ODR = Observed rate of p < .05.
EDR = Expected rate of p < .05 without bias.
ERR = Estimated replication success rate of significant results.
Full Introduction
Z-curve is a statistical tool for meta-analysis of larger sets of studies (k > 100). Although it can be used with smaller sets of studies (k > 10 significant results), confidence intervals are likely to be very wide. There are also different types of meta-analysis. The core application of meta-analysis is to combine information from direct replication studies. that is studies that test the same hypothesis (e.g., the effect of aspirin on blood pressure). The most widely used meta-analytic tools aim to estimate the average effect size for a set of studies with the same research question. A second application is to quantitatively review studies on a specific research topic. These studies are called conceptual replication studies. They test the same or related hypothesis, but with different experimental procedures (paradigms). The main difference between meta-analysis of direct and conceptual replication studies is that we would expect less variability in population effect sizes (not the estimates in specific samples) in direct replications, whereas variability is expected to be higher in conceptual replication studies with different experimental manipulations and dependent variables.
Z-curve can be applied to meta-analysis of conceptual replication studies, but it was mainly developed for a third type of meta-analysis. These meta-analyses examine sets of studies with different hypotheses and research designs. Usually, these studies share a common feature. For example, they may be published in the same journal, belong to a specific scientific discipline or sub-discipline, or a specific time period. The main question of interest here is not the average effect size that is likely to vary widely from study to study. The purpose of a z-curve analysis is to examine the credibility or statistical integrity of a set of studies. The term credibility is a broad term that covers many features of a study. Z-curve focuses on statistical power as one criterion for the credibility of a study. To use z-curve and to interpret z-curve results it is therefore important to understand the concept of statistical power. Unfortunately, statistical power is still not part of the standard education in psychology. Thus, I will provide a brief introduction to statistical power.
Statistical Power
Like many other concepts in statistics, statistical power (henceforth power, the only power that does not corrupt), is a probability. To understand power, it is necessary to understand the basics of null-hypothesis significance testing (NHST). When resources are insufficient to estimate effect sizes, researchers often have to settle for the modest goal to examine whether a predicted positive effect (exercise increases longevity) is positive, or a predicted negative effect is negative (asparin lowers blood pressure). The common approach to do so is to estimate the effect size in a sample, estimate the sampling error, compute the ratio of the two, and then compute the probability that the observed effect size or an even bigger one could have been obtained without an effect; that is, a true effect size of 0. Say, the effect of exercise on longevity is an extra 2 years, the sampling error is 1 year, and the test statistic is 2/1 = 2. This value would correspond to a p-value of .05 that the true effect is positive (not 2 years, but greater than 0). P-values below .05 are conventionally used to decide against the null hypothesis and to infer that the true effect size is positive if the estimate is positive or that the true effect is negative if the estimate is negative. Now we can define power. Power is the probability of obtaining a significant result, which typically means a p-value below .05. In short,
Power is the probability of obtaining a statistically significant result.
This definition of power differs from the textbook definition of power because we need to distinguish between different types of powers or power calculations. The most common use of power calculations relies on hypothetical population effect sizes. For example, let’s say we want to conduct a study of exercise and longevity without any prior studies. Therefore, we do not know whether exercise has an effect or how big the effect is. This does not stop us from calculating power because we can just make assumptions about the effect size. Let’s say we assume the effect is two years. The main reason to compute hypothetical power is to plan sample sizes of studies. For example, we have information about the standard deviation of people’s life span and can compute power for hypothetical sample sizes. A common recommendation is to plan studies with 80% power to obtain a significant result with the correct sign.
It would be silly to compute the hypothetical power for an effect size of zero. First, we know that the probability of a significant result without a real effect is set by the research. When they use p < .05 as a rule to determine significance, the probability of obtaining a significant result without a real effect is 5%. If they use p < .01, it is 1%. No calculations are needed. Second, researchers conduct power analysis to find evidence for an effect. So, it would make no sense to do the power calculation with a value of zero. This is null hypothesis that researchers want to reject, and they want a reasonable sample size to do so.
All of this means that hypothetical power calculations assume a non-zero effect size and power is defined as the conditional probability to obtain a significant result for a specified non-zero effect size. Z-curve is used to compute a different type of power. The goal is to estimate the average true power of a set of studies. This average can be made up of a mix of studies in which the null hypothesis is true or false. Therefore, z-curve estimates are no longer conditional on a true effect. When the null hypothesis is true, power is set by the significance criterion. When there is an effect, power is a function of the size of the effect. All of the discussion of conditional probability is just needed to understand the distinction between the definition of power in hypothetical power calculations and in empirical estimates of power with z-curve. The short and simple definition of power is simply the probability of a study to produce a significant result.
Populations of Studies
Brunner and Schimmack (2020) introduce another distinction between power estimates that is important for the understanding of z-curve. One population of studies are all studies that have been conducted independent of the significance criterion. Let’s assume researchers’ computers were hooked up to the internet and whenever they conduct a statistical analysis, the results are stored in a giant database. The database will contain millions of p-values, some above .05 and others below .05. We could now examine the science-wide average power of null hypothesis significance tests. In fact, it would be very easy to do so. Remember, power is defined as the probability to obtain a significant result. We can therefore just compute the percentage of significant results to estimate average power. This is no different than averaging the results of 100,000 roulette games to see how often a table produces “red” or “black” as an outcome. If the table is biased and has more power to get “red” results, you could win a lot of money with that knowledge. In short,
The percentage of significant results in a set of studies provides an estimate of the average power of the set of studies that was conducted.
We would not need a tool like z-curve, if power estimation were that easy. The reason why we need z-curve is that we do not have access to all statistical tests that were conducted in science, psychology, or even a single lab. Although data sharing is becoming more common, we only see a fraction of results that are published in journal articles or preprints on the web. The published set of results is akin to the proverbial tip of the iceberg, and many results remain unreported and are not available for meta-analysis. This means, we only have a sample of studies.
Whenever statisticians draw conclusions about populations from samples, it is necessary to worry about sampling bias. In meta-analyses, this bias is known as publication bias, but a better term for it is selection bias. Scientific journals, especially in psychology, prefer to publish statistically significant results (exercise increases longevity) over non-significant results (exercise may or may not increase longevity). Concerns about selection bias are as old as meta-analyses, but actual meta-analyses have often ignored the risk of selection bias. Z-curve is one of the few tools that can be used to detect selection bias and quantify the amount of selection bias (the other tool is the selection model for effect size estimation).
To examine selection bias, we need a second approach to estimate average power, other than computing the average of significant results. The second approach is to use the exact p-values of a study (e.g., p = .17, .05, .005) and to convert them into z-values (e.g., z = 1, 2, 2.8). These z-values are a function of the true power of a study (e.g., a study with 50% power has an expected z-value of ~ 2), and sampling error. Z-curve uses this information to obtain a second estimate of the average power of a set of studies. If there is no selection bias, the two estimates should be similar, especially in reasonably large sets of studies. However, often the percentage of significant result (power estimate 1) is higher than the z-curve estimate (power estimate 2). This pattern of results suggests selection for significance.
In conclusion, there are two ways to estimate the average power of a set of studies. Without selection bias, the two estimates will be similar. With selection bias, the estimate based on counting significant results will be higher than the estimate based on the exact p-values.
Figure 1 illustrates the extreme scenario that the true power of studies was just 40%, but selection bias filtered out all non-significant results.
Figure 1. Histogram of z-scores from 1,984 significant tests (based on a simulation of 5,000 studies with 40% power). The solid red line represents the z-curve fit to the distribution of observed z-values. The dashed red line shows the expected distribution without selection bias. The vertical red line shows the significance criterion, p < .05 (two-sided, z ~ 2). ODR = Observed Discovery Rate, EDR = Expected Discovery Rate, ERR = Expected Replication Rate. FDR = False Positive Risk, not relevant for the Introduction.
The figure shows a z-curve plot. Understanding this plot is important for the use of z-curve. First, the plot is a histogram of absolute z-values. Absolute z-values are used because in field-wide meta-analyses the sign has no meaning. In one study, researchers predicted a negative result (aspirin decreases blood pressure) and in another study they predicted a positive result (exercises increases longevity). What matters is that the significant result was used to reject the null hypothesis in either direction. Z-values above 6 are not shown because they are very strong, imply nearly 100% power. The critical range of z-scores are z-scores between 2 (p = .05, just significant) and 4 (~ p = .0001).
The z-curve plot makes it easy to spot selection for significance because there are many studies with just significant results (z > 2) and no studies with just not-significant results that are often called marginally significant results because they are used in publications to reject the null hypothesis with a relaxed criterion. A plot like this cannot be produced by sampling error.
In a z-curve plot, the percentage of significant results is called the observed discovery rate. Discovery is a term used in statistic for a significant result. It does not mean a breaking-news discovery. It just means p < .05. The ODR is 100% because all results are significant. This would imply that all studies tested a true hypothesis with 100% power. However, we know that this is not the case. Z-curve uses the distribution of significant z-scores to estimate power, but there are two populations of power. One population is all studies, including the missing non-significant results. I will explain later how z-curve estimates power. Here it is only important that the estimate is 40%. This estimate is called the expected discovery rate. That is, if we could get access to all missing studies, we would see that only 40% of the studies were significant. Expected therefore means without selection bias and open access to all studies. The difference between the ODR and EDR quantifies the amount of selection bias. Here selection bias inflates the ODR from 40% to 100%.
It is now time to introduce another population of studies. This is the population of studies with significant results. We do not have to assume that all of these studies were published. We just assume that the published studies were not selected based on their p-values. This is a common assumption in selection models. We will see later how changing this assumption can change results.
It is well known that selection introduces bias in averages. Selection for significance, selects studies that had positive sampling error that produced z-scores greater than 2, while the expected z-score without sampling error is only 1.7, not significant on its own. Thus, a simple power calculation for the significant results would overestimate power. Z-curve corrects for this bias and produces an unbiased estimate of the average power of the population of studies with significant results. This estimate of power after selection for significance is called the expected replication rate (ERR). The reason is that average power of the significant results predicts the percentage of significant results if the studies with significant results were replicated exactly, including the same sample sizes. The outcome of this hypothetical replication project would be 40% significant results. The decrease from 100% to 40% is explained by the effect of selection and regression to the mean. A study that had an expected value of 1.7, but sampling error pushed it to 2.1 and produced a significant result is unlikely to have the same sampling error and produce a significant result again.
At the bottom of z-curve 3.0, you see estimates of local power. These are average power estimates for ranges of z-values. The default is to use steps of z = .05. You see that the strength of the observed z-values does not matter. Z-values between 0 and 0.5 are estimated to have 40% power as do z-values between 5.5 and 6. This happens when all studies have the same power. When studies differ in power, local power increases because studies with higher power are more likely to produce larger z-values.
When all studies have the same power, power is said to be homogenous. When studies have different levels of power, power is heterogeneous. Homogeneity or small heterogeneity in power imply that it is easy to infer the power of studies with non-significant results from studies with significant results. The reason is that power is more or less the same. Some selection models like p-curve assume homogeneity. For this reason, it is not necessary to distinguish populations of studies with or without significant results. It is assumed that the true power is the same for all studies, and if the true power is the same for all studies, it is also the same for all subsets of studies. This is different for z-curve. Z-curve allows for heterogeneity in power, and z-curve 3.0 provides a test of heterogeneity. If there is heterogeneity in power, the ERR will be higher than the EDR because studies with higher power are more likely to produce a significant result (Brunner & Schimmack, 2020).
To conclude, the introduction introduced basic statistical concepts that are needed to conduct z-curve analyses and to interpret the results correctly. The key constructs are
Meta-Analysis: the statistical analysis of results from multiple studies Null Hypothesis Significance Testing Statistical Significance: p < .05 (alpha) (Statistical) Power: the probability of obtaining a significant result Conditional Power: the probability of obtaining a significant result with a true effect Populations of Studies: A set of studies with a common characteristic Set of all studies: studies with non-significant and significant results Selection Bias: An overrepresentation of significant results in a set of studies (Sub)Set of studies with significant results: Subset of studies with p < .05 Observed Discovery Rate (ODR): the percentage of significant results in a set of studies Expected Discovery Rate (EDR): the z-curve estimate of the discovery rate based on z-values Expected Replication Rate (ERR): the z-curve estimate of average power for the subset of significant results.
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