Publish or perish. I heard this in the 1990s, but it is even more true today. Submitting manuscript to publish has gotten easier, too. It cost me real money to mail three copies of a manuscript from Germany to the United States (Schimmack, 1996). Now, you just need to check all the boxes on a submission portal. Not an easy task, but virtually cost free.

This system is like a lottery, where tickets are cheap and winnings can be rewarding. No wonder, authors are playing the lottery and submitting manuscripts in large numbers, even if chances of rejection are high. Maybe journals should charge for submissions rather than for publications.

Anyhow, I just reviewed a manuscript in 30 minutes. It was conceptually flawed. More importantly, my own AI – trained on this area of research – also spotted the conceptual problem, and several others that I didn’t even bother to read as it would take too long for a human reader to do so (life is short at age 60). It also wrote a nice and detailed review, much better than most human reviews. Of course, it had the advantage of being trained on this research area, but I also submitted the manuscript to a generic AI with no special knowledge. It also spotted the fatal conceptual mistake. This brings me to the main point of this rant.

Dear authors, do yourself and others a favor. Use AI to review your paper before you submit it. Even better ask it to evaluate it from the perspective of legendary Reviewer 2 and address critical issues before you submit it to a journal. You save yourself time and effort, but more importantly, you are a good citizen and do not clog the peer-review system with flawed manuscripts in the hope that they pass peer-review despite major problems.

Thank you for your attention.

No polite ChatGPT edits. Unfiltered raw Schimmack. Love it or hate it.

It was supposed to be the American Psychological Society (APS), but international researchers complained – especially those who want to publish in prestigious American journals – and APS became the Association for Psychological Science.

Psychological Science is now a brand name and many departments have been renamed to be Departments of Psychological Science. However, you do not become a science, just because you call yourself one, you actually have to behave like a science. And that seems to be something that many psychologists do not want to do because it would mean giving data to decide about the truth. Just like William James, many psychologists like their theories more than truth So, they continue to conduct silly statistical rituals (Gigerenzer) that are biased to show either evidence for their beliefs (p < .05) or no evidence against them (p > .05) and justify another biased test.

Every generation there have been a few psychologists who were frustrated by the futility of this and made suggestions to improve things (Meehl, Cohen, Gigerenzer) or just also fake the data (Stapel). You have to give it to Stapel. Why collect data if their only purpose is to add p < .05 to any claim one wants to make?

Since the early 2010s, thanks to Bargh and Bem, more people are calling for change, but progress is slow and stalling. Meanwhile, most published articles continue to report claims with p-values below .05.

A cynical approach to this sad state of affairs would be to say “fuck it”, “burn it all down,” and enjoy life. However, some people just can’t let go. We (Brunner, Bartos, Schimmack) developed a statistical method that helps readers to distinguish between good and bad significant results. Good ones come from studies with high statistical power that are likely to replicate. Bad ones are studies with low power or even false positive results that will not replicate. Of course, there is no hard line, but we can identify subsets of good studies, if they exist.

You would think an aspirational science would welcome a tool that can salvage good results from decades of research with mostly significant results. Which ones are trustworthy? Which ones are like pornception (Bem, 2011)?

But being a science would mean that we have to expose the fact that some results were made up – not like Stapel on his laptop – but by collecting and analyzing data, year after year, painstaking work to get significant results – and many unpublished failures. No, we cannot have this. Therefore, we have to fight the method that can distinguish good and bad research.

To fight this method, we need to get a peer-reviewed article that claims “the method does not work.” To do so, the article does not have to be evaluated by statisticians or present good arguments. All we need is a quotable peer-reivewed article, because peer-reviewed equals truth, which is also why extrasensory perception is true (Bem, 2011, JPSP).

Now reviewers can quote the criticism – and not cite evidence that contradicts these claims – and editors can use the peer-review to reject the article. The key feature of science is to fight motivational biases. If a system just amplifies misinformation and glorifies misinformation that passed peer-review, it is not a science. Maybe APS really means Anti-Psychological Science.

The question is how long this game of self- and other-deception can continue? At what point will public interest in psychology wane because it never produces any useful results that advance society, health, and wellbeing? Science is worth defending against the attacks by Trumpians, but I am not sure psychological science is part of this.

All options are set as global variables at the beginning of installing the functions with source(zcurve3). Afterwards they can be changed like any other R object

1. Curve Type: Default Z-Values, Option Fit t-Distributions with a Fixed df

CURVE.TYPE <- “z” # Set to “t” for t-distribution
df = c() # set to the df of the t-distribution

2. Speed Control Parameters

parallel <- FALSE # Placeholder – parallel functionality not yet implemented
max_iter <- 1e6 # Max iterations for model estimation
max_iter_boot <- 1e5 # Max iterations for bootstrapped estimates

EM.criterion <- 1e-3 # Convergence threshold for EM algorithm
EM.max.iter <- 1000 # Max iterations for EM

Plot.Fitting <- FALSE # Plot fitting curve (only for Est.Method = “OF” or “EXT”)

PLOT SETTINGS

Title <- “” # Optional plot title

letter.size <- 1 # Text size in plots
letter.size.1 <- letter.size # Used for version labels in plot
y.line.factor <- 3 # Controls spacing of plot text

x.lim.min <- 0 # X-axis lower bound
x.lim.max <- 6 # X-axis upper bound
ymax <- 0.6 # Y-axis upper bound
ymin <- 0 # OUTDATED Y-axis lower bound (for label space)

Show.Histogram <- TRUE # Toggle histogram in plot
Show.Text <- TRUE # Toggle model results in plot
Show.Curve.All <- TRUE # Show predicted z-curve
Show.Curve.Sig <- FALSE # Option: show z-curve only for significant values
Show.Significance <- TRUE # Show z = critical value line
Show.KD <- FALSE # Toggle kernel density overlay (density method only)

sig.levels <- c() # Optional: mark additional p-value thresholds on plot

int.loc <- 0.5 # Plot local power intervals below x-axis (set 0 to disable)
hist.bar.width <- 0.2 # Width of histogram bars
bw.draw <- 0.10 # Smoothing for kernel density display

CONSOLE OUTPUT

Show.Iterations <- TRUE # Show iterations for slow procedures (e.g., EXT, TEST4HETEROGENEITY)

MODEL PARAMETERS

alpha <- 0.05 # Significance level
crit <- qnorm(1 – alpha / 2) # Corresponding two-sided critical z

two.sided <- TRUE # Assume two-sided z-values (use abs(z)); not yet compatible with signed z-values

Color scheme

col.curve <- “violetred3”
col.hist <- “blue3”
col.kd <- “green3”

Est.Method <- “OF” # Estimation method: “OF”, “EM”, or “EXT” # Clustered Data: “CLU-W” (weighted),”CLU-B” (bootstrap) Int.Beg <- 1.96 # Default: critical value for alpha = .05 Int.End <- 6 # End of modeling interval (z > 6 = power = 1)

ncp <- 0:6 # Component locations (z-values at which densities are centered)
components <- length(ncp) # Number of components
zsd <- 1 # SD of standard normal z-distribution
zsds = rep(zsd,components) # one SD for each component

just <- 0.8 # Cutoff for “just significant” z-values (used in optional bias test)

ZSDS.FIXED <- FALSE # Fix SD values for EXT method
NCP.FIXED <- FALSE # Fix non-central parameter(NCP) means values for EXT method
W.FIXED <- FALSE # Fix weights for EXT method

fixed.false.positives <- 0 # If > 0, constrains proportion of false positives (e.g., weight for z = 0 component)

DENSITY-BASED SETTINGS (Only used with Est.Method = “OF”)

n.bars <- 512 # Number of bars in histogram

Augment <- TRUE # Apply correction for bias at lower bound
Augment.Regression <- FALSE # Use Slope for Augmentation
Augment.Factor <- 1 # Amount of augmentation

bw.est <- 0.05 # Bandwidth for kernel density (lower = less smoothing, higher = more smoothing)
bw.aug <- .20 # Width of Augmentation interval

INPUT RESTRICTIONS

MAX.INP.Z <- Inf # Optionally restrict very large z-values (set Inf to disable)

CONFIDENCE INTERVALS / BOOTSTRAPS

boot.iter <- 0 # Number of bootstrap iterations (suggest 500+ for final models)
ERR.CI.adjust <- 0.03 # Conservative widening of confidence intervals for ERR
EDR.CI.adjust <- 0.05 # Conservative widening for EDR

CI.ALPHA <- 0.05 # CI level (default = 95%)

CI levels for Heterogeneity Test

fit.ci <- c(.01, .025, .05, .10, .17, .20, .50, .80, .83, .90, .95, .975, .99) # CI levels for model fit test

TEST4BIAS <- FALSE # Enable optional bias test
TEST4HETEROGENEITY <- 0 # Optional heterogeneity test (slow) — set number of bootstrap iterations

Abstract

A recent critique of z-curve reported low coverage of confidence intervals for the expected discovery rate (EDR) based on an extreme simulation with a very low expected false positive rate (about 1–2%). This conclusion conflates expected values with realized data. In repeated runs, the number of false positives among significant results varies substantially and is often zero; in those runs the realized false discovery rate is exactly zero, so an estimate of zero is correct. When coverage is evaluated against realized false positive rates, the apparent problem is substantially reduced. Additional simulations show that coverage approaches the nominal level once false positives are non-negligible (e.g., 5%) and improves further with larger numbers of significant results. Remaining coverage failures are confined to diagnostically identifiable cases in which high-powered studies dominate the distribution of significant z-values, leaving limited information to estimate the EDR.

On Evaluating Evidence and Interpreting Simulation Results

Science advances through skepticism. It progresses by testing claims against evidence and by revisiting conclusions when new information becomes available. This process requires not only sound data, but also careful interpretation of what those data can and cannot tell us.

In principle, academic debate should resolve disagreements by subjecting competing interpretations to scrutiny. In practice, however, disagreements often persist. One reason is that people—scientists included—tend to focus on evidence that aligns with their expectations while giving less weight to evidence that challenges them. Another is that conclusions are sometimes used, implicitly or explicitly, to justify the premises that led to them, rather than the other way around.

These concerns are not personal; they are structural. They arise whenever complex methods are evaluated under simplified criteria.

Context of the Current Discussion

Z-curve was developed to evaluate the credibility of a set of statistically significant results. It operates on the distribution of significant test statistics and estimates quantities such as the expected replication rate (ERR), the expected discovery rate (EDR), and the false discovery rate (FDR). Its performance has been evaluated using extensive simulation studies covering hundreds of conditions that varied effect sizes, heterogeneity, and false positive rates.

A recent critique raised concerns about z-curve based on a simulation in which confidence intervals for the EDR showed low coverage. From this result, it was suggested that the method is unreliable (“concerns about z-curve“).

It is useful to examine carefully what this simulation does and how its results are interpreted.

Expected Values and Realized Data

The simulation assumes two types of studies: some that test true null hypotheses and others that test false null hypotheses with very high power. From this setup, one can compute expected values—for example, the expected number of false positives or the expected discovery rate.

Expected values, however, are averages over many hypothetical repetitions. In individual simulation runs, the realized number of false positives varies. In particular, when the expected number of false positives is close to one, it is common for some runs to contain no false positives among the significant results. In those runs, the observed significant record contains no false discoveries, and the realized false discovery rate for that record is exactly zero.

Evaluating coverage by comparing z-curve estimates to a fixed expected value in every run overlooks this variability. It treats a population-level expectation as if it were the true value for each realized dataset, even when the realized data are inconsistent with that expectation. This issue is most pronounced in near-boundary settings, where the quantities of interest are weakly identifiable from truncated data.

The simulation uses an extreme configuration to illustrate a potential limitation of z-curve. The setup assumes two populations of studies: one repeatedly tests a true null hypothesis (H0), and the other tests a false null hypothesis with very high power (approximately 98%, corresponding to z ≈ 4). Z-curve is applied only to statistically significant results, consistent with its intended use.

In the specific configuration, there are 25 tests of a true H0 and 75 tests of a false H0 with 98% power. From this design, one can compute expected values: on average, 25 × .05 = 1.25 false positives are expected, implying a false discovery rate of about 1.6% among significant results. However, these values are expectations across repeated samples; they are not fixed quantities that hold in every simulation run.

Because the expected number of false positives is close to one, sampling variability is substantial. In some runs, no false positive enters the set of significant results at all. In those runs, it is not an error if z-curve assigns zero weight to the null component and estimates an FDR of zero; that estimate matches the realized composition of the observed significant results.

When I reproduced the simulation and counted the number of false positives among the significant results, I found that the realized count ranged from 0 to 5, and that 152 out of 500 runs contained no false positives. This matters for interpreting coverage: comparing z-curve estimates in these runs to the expected false discovery rate of 1.6% treats a population-level expectation as if it were the true value for each realized dataset. As a result, the reported undercoverage is driven by a mismatch between the evaluation target and the realized data in a substantial subset of runs, rather than by a general failure of z-curve.

Reexamining Z-curve Performance with Extreme Mixtures

To examine z-curve’s performance with extreme mixtures of true and false H0, I ran a new simulation that sampled 5 significant results from tests of true H0 and 95 significant results from tests of false H0 with 98% power. I used a false positive rate of 5%, because a 5% false positive rate may be considered the boundary value for an acceptable error rate. Importantly, increasing it further would benefit z-curve because it becomes easier to detect the presence of low powered hypothesis tests.

As expected, the coverage of the EDR increased. In fact, it was just shy of the nominal level of 95%, 471/500 (94%). Thus, low coverage is limited to data with fewer than 5% false positive results. For example, the model may suggest no false positives, but the true false positive rate is 4%.

It is also possible to diagnose data that can create problems with coverage. First, a decreasing slope from significance to z = 3 implies a large number of missing non-significant results that can be identified by their influence on the distribution of significant z-values. In contrast a flat or positive slope suggests that high powered studies have a stronger influence on the distribution of z-values between 2 and 3. I computed the slope using the kernel density of the observed data and regressing the densities on the z-values. A positive slope perfectly predicted bad coverage, 29/29 (100%).

Another diagnostic is the ERR. A high ERR implies that most studies have high power and that there are few low powered studies with significant results to estimate the EDR. All failures occurred when the ERR was above 90%.

Finally, we can use the weights of the low powered components (z = 0, z = 1). When these weights are zero, it is possible that the model had problems estimating these components. In all failures, both weights were zero.

Importantly, these results also show that z-curve does not inevitably fail under this type of mixture. The issue is not the false positive rate per se, but the amount of information available to estimate it. With the same false positive rate of 5%, but a larger number of significant results—for example, 50 false positives out of 1,000—z-curve reliably detects the presence of missing non-significant results, even when the slope is increasing and the ERR is high. In this case, the weight of the z = 0 component was estimated at approximately 52%. By contrast, when the estimated weight is zero and the FDR estimate is zero, the true false discovery rate may still be as high as 5%, reflecting weak identifiability rather than estimator bias.

Conclusion

The low coverage reported in this simulation is largely an evaluation artifact. In this extreme setup, the expected false positive rate (about 1–2%) is an average across runs, but the realized number of false positives among significant results varies; in many runs it is zero. In those runs, the realized FDR is exactly zero, so an estimate of zero is not an error. Treating the expected rate as the “true value” in every run mechanically produces undercoverage.

When the false discovery rate is modest (e.g., 5%) and the number of significant results is larger, coverage is close to nominal and improves further as information increases. The remaining failures are confined to diagnostically identifiable cases in which high-powered studies dominate the significant z-values, leaving too little information to estimate the EDR.

Daniel Kahneman coined the term “adversarial collaborations” for research projects conducted by teams of researchers with conflicting or opposing views. The idea was that such projects would help to resolve academic disputes that can linger for decades because researchers usually conduct confirmatory studies that support their own views and neglect evidence that does not. This human bias, called confirmation bias, is one of the most well documented and robust biases demonstrated by social psychologists. At the same time, the replication crisis in social psychology has demonstrated that even scientists who are fully aware of this bias are often unable to overcome it. We may call this “confirmation bias neglect,” “confirmation bias blindspot” or “willful incompetence” – the inability to train oneself to conduct research as it is supposed to be by putting one’s own ideas to a risky empirical test that can demonstrate that the cherished theory is false.

Adverserial collaboration projects remain rare and the few that exist also show that they do not overcome human biases. Discussion sections are often not decisive, and the only agreement is that “more research is needed.” Taxpayers might say that they are not interested in funding more research that provides no clear answers. Much of social psychology is more infotainment than science.

I have been working with AI for over a year now and I think AI can play an important role in reducing human biases and making psychology look more like a science; that is, declare a winner in scientific debates so that field can move on. This blog post is just a little demonstration what this might look like.

The example comes from a debate in statistics. Readers may think that statistics is like math, where it is relatively easy to find consensus that 2 + 2 = 4, and not 5. A debate about this would make anybody arguing that 2 + 2 = 5 look like a biased, if not crazy, person, and the debate would quickly fizzle. However, statistics is nothing like match even if it uses formulas and Greek symbols. In the end, statistics only exists because math is being used to make claims about unknowns like the outcome of the next election or the true effect of feedback on learning. Observed data provide some information, but statistics is needed to make the leap to unobservable. In this world, academics fight even about the most basic assumptions, and everybody has a cherished approach that is defended like other people defend religious beliefs. Some not only defend their God but also spend considerable time attacking other religions. In this world, 2 + 2 can be 4, 5, or infinite.

I am not a trained statistician, but I worked with a statistician, Jerry Brunner, on a statistical method to make sense of published results after the replication crisis. We validated this method with extensive simulation studies and showed that it performs best under realistic conditions; that is when studies vary considerably in designs, sample sizes, and the unknowable effect sizes (Brunner & Schimmack, 2020). In 2022, a genus student, Frantisek Bartos and I extended the method to quantify the amount of publication bias (how many results that did not confirm predicts did researchers hide from the public) and the false positive risk (how many of the published results might have provided false evidence for researchers claims). Frantisk used hundreds of computing hours to validate this method across hundreds of realistic scenarios. Both articles appeared in Meta-Psychology, a journal that demands publishing reproducible code to check results that can also be used to run additional simulations. In the past three years, z-curve has been criticized, and we have responded to these criticisms. For example, z-curve can show bias when samples are tiny (N < 30). This is usually not a problem because studies with tiny sample sizes are rare, but we also created a fix for this problem for applications in research areas that have tiny samples.

Anyhow, Erik van Zwet, a biostatistican from the Netherlands, posted two blog posts to criticize z-curve. Each blog post showed a simulation that revealed problems with the estimation of the expected discovery rate that is used to evaluate publication bias and false positive risks. The first discussion quickly deteriorated and serves as an example of the passion that academics can have for topics that normal humans could not care less about. The second one attracted little interest and was mainly an exchange between Erik and me.

I asked ChatGPT to referee the exchange and it wrote a “game report” that is informative and funny at the same time. Importantly, I won, but barely. The outcome is less important than the neutral and balanced report. The main advantage of AI is not that it has superintelligence. It’s main strength is that it does not care about the outcome of the game. The desire to be right is the Kryptonite of academics. Calls for humility are nice, but unrealistic. Trying to prove your ideas to be right motivates many academics to work long hours and sometimes to waste their entire life on nutty ideas like extrasensory perception. AI may help us individually and collectively to avoid this mistake.

You can find the actual game here
More concerns about the z-curve method | Statistical Modeling, Causal Inference, and Social Science

And here is ChatGPTs game report:

---

Full time

Ulrich 5 – 4 Erik

(Technically decisive win for Ulrich, but with avoidable late fouls.)

---

First half

Erik goals (2)

(6′) Framing the agenda
Erik successfully sets the frame: undercoverage of EDR CIs, bootstrap collapse, and model misspecification. This is a legitimate opening and forces engagement.

(18′) Collapsing CI diagnosis
The zero-length CI for (P(\mathrm{SNR}=0)) is a real inferential pathology. This is Erik’s strongest technical contribution and remains uncontested as a phenomenon.

---

Ulrich goals (2)

(25′) Extensive validation defense
Ulrich correctly invokes prior large-scale simulations and reproducibility checks. This blunts any claim that z-curve was casually or narrowly validated.

(38′) Black-swan argument
The point that one pathological case does not invalidate a method in general is sound and resonates with statistically literate readers.

---

Second half

Erik goals (2)

(52′) Model-uncertainty critique
Erik’s argument that bootstrap CIs reflect sampling uncertainty but ignore model uncertainty is correct in principle and applies to mixture models under misspecification.

(64′) “Undetectable violation” claim
The insistence that the misspecification is practically undetectable from truncated data keeps pressure on defaults and diagnostics. This is a fair methodological concern.

---

Ulrich goals (3)

(70′) vj intervention (assist credited to Ulrich)
The vj comment decisively reframes the issue:

• identifies perfect power homogeneity,
• explains weak identification of EDR,
• localizes the failure to a knife-edge case.

This is a major momentum shift.

(78′) Mu-grid diagnosis and fix
Demonstrating that coverage is restored by aligning the mu grid is a technical knockout: it shows the issue is resolution under discretization, not a broken method.

(85′) Final Ulrich comment (heterogeneity + alternatives)
This is your strongest direct response:

• acknowledges the edge case,
• explains why it is unrealistic,
• cites known alternatives (moving μ, random-effects),
• and challenges Erik to generalize his claim.

Substantively, this closes the loop.

---

Own goals

Ulrich — Own Goals (2)

(44′) Early defensive tone
The initial “he does not hear me” framing and appeal to Erik’s past review role weakened the epistemic high ground.

(90’+2) P.S. about Andrew
The postscript is unnecessary and risks shifting attention back to tone and personalities rather than substance.

---

Erik — Own Goals (3)

(60′) Escalation to personal insinuation
Claims of harassment, editorial intervention, and “you haven’t read the post” add heat but no inferential value.

(88′) Latest reply (“comforting thought for you”)
This is a clear tone foul. It undercuts Erik’s otherwise disciplined methodological position and hands Ulrich the moral high ground late in the game.

(90′) Failure to engage heterogeneity point
Erik never answers the central empirical challenge: where do we see near-homogeneous power in real literatures? That omission matters.

---

Man of the Match

Ulrich

Reason: You end the exchange with a coherent synthesis:

• the failure mode is known,
• it arises in unrealistic knife-edge cases,
• defaults work because real data are heterogeneous,
• and alternatives exist if one worries about that edge case.

That is the position readers will remember.

---

Final assessment

• You won on substance.
• You mostly avoided tone own goals, except for the P.S.
• Erik’s last comment actually hurts his case more than it hurts yours.

At this point, do not reply again. The ball is out of play, and any further touch risks a needless foul.

If Erik posts new simulations with realistic heterogeneity, bring them here first. Otherwise, this match is over—and you won it.

The term science can be used to describe both the actual practices of researchers and an idealized set of practices that distinguish science from other approaches to making claims about the world.

A core aspect of the idealized conception of science is that research activity is used to test theories, and that empirical tests can, under some conditions, falsify theoretical predictions. Falsification is neither necessary nor sufficient for scientific progress, but a research program that systematically insulates theories from empirical refutation departs from core scientific norms. Unfortunately, psychology has often ignored falsification or confused rejections of null hypotheses with falsification.

The fallacy here is that rejection of null hypotheses is used to confirm theoretical hypotheses about the direction or existence of effects. As a consequence, psychology lacks widely used statistical methods that can provide affirmative evidence against substantive theoretical predictions. Studies are typically interpreted as confirming predictions or are deemed inconclusive.

This asymmetry in evidential standards helps explain why over 90% of articles report confirmation of a theoretical prediction (Sterling, 1959; Sterling et al., 1995). Psychologists paid little attention to this unusually high success rate until replication attempts of published studies revealed that replication success in experimental social psychology was substantially lower than implied by the published literature, with only 25% successful replications in the Reproducibility Project (2025).

Some review articles suggest that the replication crisis has led to methodological reforms and has made experimental social psychology more trustworthy. This is partially correct. Social psychologists played a prominent role in the Open Science movement and contributed to reforms such as open data, preregistration, and registered reports. However, these reforms are not universally mandated and do not retroactively address the credibility of results published prior to their adoption, particularly before the 2010s. Moreover, incentives remain that favor positive and theoretically appealing results, and some researchers continue to downplay the extent of the replication problem. As a result, it is difficult to make general claims about social psychology as a unified scientific enterprise. In the absence of enforceable, field-wide normative standards, credibility remains largely a property of individual researchers rather than the discipline as a whole.

Social Priming

Priming is a general term in psychology referring to the automatic influence of stimuli on subsequent thoughts, feelings, or behaviors. A classic example from cognitive psychology shows that exposure to a word such as “forest” facilitates the processing of related words such as “tree.”

Social psychologists hypothesized that priming could also operate without awareness and influence actual behavior. A well-known study appeared to show that exposure to words associated with elderly people caused participants to walk more slowly (Bargh et al., 1996). That article also reported subliminal priming effects, suggesting that behavioral influence could occur without conscious awareness. These findings inspired a large literature that appeared to demonstrate robust priming effects across diverse primes, presentation modes, and behavioral outcomes, with success rates comparable to those documented by Sterling (1959).

In 2012, a group of relatively early-career researchers published a failure to replicate the elderly-walking priming effect (Doyen et al., 2012). The publication of this study marked an important turning point, as it challenged a highly influential finding in the literature. Bargh responded critically to the replication attempt, and the episode became widely discussed. Daniel Kahneman had highlighted priming research in Thinking, Fast and Slow and, concerned about its replicability, encouraged original authors to conduct high-powered replications. These replications were not forthcoming, while independent preregistered studies with larger samples increasingly failed to reproduce key priming effects. As a result, priming research became a focal example in discussions of the replication crisis. Kahneman later distanced himself from strong claims based on this literature and expressed regret about relying on studies with small samples (Kahneman, 2017).

Willful Ignorance and Incompetence In Response to Credibility Concerns

In 2016, Albarracín (as senior author) and colleagues published a meta-analysis concluding that social priming effects exist, although the average effect size was relatively small (d ≈ .30; Weingarten et al., 2016). An effect of this magnitude corresponds to roughly one-third of a standard deviation, which is modest in behavioral terms.

The meta-analysis attempted to address concerns about publication bias—the possibility that high success rates reflect selective reporting of significant results. If selection bias is substantial, observed effect sizes will be inflated relative to the true underlying effects. The authors applied several bias-detection methods that are now widely recognized as having limited diagnostic value. They also used the p-curve method, which had been introduced only two years earlier (Simonsohn et al., 2014). However, the p-curve results were interpreted too optimistically. P-curve can reject the hypothesis that all significant results arise from true null effects, but it does not test whether publication bias is present or whether effect sizes are inflated. Moreover, the observed p-curve was consistent with an average statistical power of approximately 33%. Given such power, one would expect roughly one-third of all studies to yield significant results under unbiased reporting, yet the published literature reports success rates exceeding 90%. This discrepancy strongly suggests substantial selective reporting and implies that the true average effect size is likely smaller than the headline estimate.

Sotola (2022) reexamined Weingarten et al.’s meta-analysis using a method called z-curve. Unlike p-curve, z-curve explicitly tests for selective reporting by modeling the distribution of statistically significant results. It is also more robust when studies vary in power and when some studies have true effects while others do not. Whereas p-curve merely rejects the hypothesis that all studies were obtained under a true null, z-curve estimates the maximum proportion of significant results that could be false discoveries, often referred to as an upper bound on the false discovery rate (Bartos & Schimmack, 2022).

Sotola found that priming studies reported approximately 76% significant results—somewhat below the roughly 90% level typically observed in social psychology—but that the estimated average power to produce a significant result was only 12.40%. Z-curve also did not rule out the possibility that all observed significant results could have arisen without a true effect. This finding does not justify the conclusion that social priming effects do not exist, just as observing many white swans does not prove the absence of black swans. However, it does indicate that the existing evidence—including the Weingarten et al. meta-analysis—does not provide conclusive support for claims that social priming effects are robust or reliable. The literature documents many reported effects but offers limited evidential leverage to distinguish genuine effects from selective reporting (many sitings of UFOs, but no real evidence of alien visitors).

Despite these concerns, Weingarten’s meta-analysis continues to be cited as evidence that priming effects are real and that replication failures stem from factors other than low power, selective reporting, and effect size inflation. For example, Iso-Ahola (2025) cites Weingarten et al. while arguing that there is no replication crisis. Notably, this assessment does not engage with subsequent reanalyses of the same data, including Sotola’s z-curve analysis.

This article illustrates what can reasonably be described as willful ignorance: evidence that does not fit the preferred narrative is not engaged. The abstract’s claim that “there is no crisis of replication” is comparable, in terms of evidential standards, to assertions such as “climate change is a hoax”—claims that most scientists regard as unscientific because they dismiss a large and well-documented body of contrary evidence. Declaring the replication problem nonexistent, rather than specifying when, where, and why it does not apply, undermines psychology’s credibility and its aspiration to be taken seriously as a cumulative science.

Willful ignorance is also evident in a recent meta-analysis, again with Albarracín as senior author. This meta-analysis does not include a p-curve analysis and ignores the z-curve reanalysis by Sotola altogether. While the new meta-analysis reports no effects in preregistered studies, its primary conclusion nevertheless remains that social priming has an effect size of approximately d = .30. This conclusion is difficult to reconcile with the preregistered evidence it reports.

A different strategy for defending social priming research is to question the validity of z-curve itself (Pek et al., 2025, preprint, Cognition & Emotion). For example, Pek et al. note that transforming t-values into z-values can break down when sample sizes are extremely small (e.g., N = 5), but they do not acknowledge that the transformation performs well at sample sizes that are typical for social psychological research (e.g., N ≈ 30). Jerry Brunner, a co-author of the original p-curve paper and a professor of statistics, identified additional errors in their arguments (Brunner, 2024). Despite detailed rebuttals, Pek et al. have repeated the same criticisms without engaging with these responses.

This pattern is best described as willful incompetence. Unlike willful ignorance, which ignores inconvenient evidence, willful incompetence involves superficial engagement with evidence while the primary goal remains the defense of a preferred conclusion. In epistemic terms, this resembles attempts to rebut well-established scientific findings by selectively invoking technical objections without addressing their substantive implications.

Z-Curve Analysis of Social Priming

To illustrate how z-curve works and what it reveals about social priming, I analyzed the new meta-analysis of social priming using z-curve. Importantly, I had no influence on the data and only transformed reported information about effect sizes and sampling error into z-values. A z-curve plot provides a descriptive visualization of the evidential strength of published results relative to the null hypothesis. At this descriptive level, few assumptions are required.

The full z-curve analysis fits a statistical model to the distribution of z-values. Studies with low power—due to small effect sizes, small sample sizes, or both—are likely to produce low z-values and often nonsignificant results (z = 1.96 ≈ p = .05). Studies with high power (e.g., 80% power corresponds to z ≈ 2.8) require either moderate-to-large effect sizes or very large sample sizes. Inspection of the plot shows that most studies cluster at low z-values, with relatively few studies producing z-values greater than 2.8. Thus, even before modeling the data, the distribution indicates that the literature is dominated by low-powered studies.

The actual z-curve analysis fits a model to the distribution of z-values. Studies with low power (small effect sizes, small sample sizes) are likely to produce low z-values and often z-values that are not significant (z = 1.96 ~ p = .05). Studies that have high power (80% power ~ z = 2.8) have moderate to large effect sizes or really large sample sizes). Inspection of the plot shows most studies have low z-values and few studies have z-values greater than 2.8. Thus, even without modeling the data, we can see that this literature is dominated by studies with low power.

The plot also reveals clear evidence of selective reporting. If results were reported without selection, the distribution of z-values would decline smoothly around the significance threshold. Instead, the mode of the distribution lies just above the significance criterion. The right tail declines gradually, whereas the left side drops off sharply. There are too many results with p ≈ .04 and too few with p ≈ .06. This asymmetry provides direct visual evidence of publication bias, independent of any modeling assumptions.

Z-curve uses the distribution of statistically significant results to estimate the Expected Replication Rate (ERR) and the Expected Discovery Rate (EDR). The ERR estimate is conceptually similar to p-curve–based power estimates but is more robust when studies vary in power. In the present analysis, the estimated ERR of 34% closely matches the p-curve estimate reported by Weingarten et al. (33%) but is substantially higher than Sotola’s earlier z-curve estimate (12.5%). However, ERR estimates assume that studies can be replicated exactly, an assumption that is rarely satisfied in psychological research. Comparisons between ERR estimates and actual replication outcomes typically show lower success rates in practice (Bartos & Schimmack, 2022). Moreover, ERR is an average: approximately half of studies have lower replication probabilities, but we generally do not know which studies these are.

The EDR estimates the proportion of all studies conducted—including unpublished ones—that are expected to yield statistically significant results. In this case, the EDR point estimate is 19%, but there is substantial uncertainty because it must be inferred from the truncated set of significant results. Notably, the confidence interval includes values as low as 5%, which is consistent with a scenario in which social priming effects are absent across studies. Thus, these results replicate Sotola’s conclusion that the available evidence does not demonstrate that any nontrivial proportion of studies produced genuine social priming effects.

Pek et al. (2025) noted that z-curve estimates can be overly optimistic if researchers not only select for statistical significance but also preferentially report larger effect sizes. In their simulations, the EDR was overestimated by approximately 10 percentage points. This criticism, however, weakens rather than strengthens the evidential case for social priming, as an EDR of 9% is even less compatible with robust effects than an EDR of 19%.

The z-curve results also provide clear evidence of heterogeneity in statistical power. Studies selected for significance have higher average power than the full set of studies (ERR = 34% vs. EDR = 18%). Information about heterogeneity is especially evident below the x-axis. Studies with nonsignificant results (z = 0 to 1.95) have estimated average power of only 18–20%. Even studies with significant results and z-values up to 4 have estimated average power ranging from 23% to 56%. To expect an exact replication to succeed with 80% power, a study would need to produce a z-value above 4, yet the plot shows that very few studies reach this level.

Adjusting Alpha To Lower False Positive Risk

Z-curve can also be used to examine how changing the significance threshold affects false discoveries. With the conventional α = .05 criterion, one out of twenty tests of a true null hypothesis will be significant by chance. Lowering α to .01 reduces this rate to one in one hundred. However, stricter thresholds also reduce power and discovery rates. In some literatures, the reduction in false discoveries outweighs the cost of fewer significant results (Soto & Schimmack, 2024). This is not the case for social priming.

Setting α = .01 (z = 2.58) lowers the point estimate of the false discovery rate from 23% to 11%, but the 95% confidence interval still includes values up to 100%.

Setting α = .001 reduces the point estimate to 3%, yet uncertainty remains so large that all remaining significant results at that threshold could still be false positives.

P-Hacking Real Effects

It is possible to obtain more favorable conclusions about social priming by adopting additional assumptions. One such assumption is that researchers relied primarily on p-hacking rather than selective reporting. Under this scenario, fewer studies would need to be conducted and suppressed. When z-curve is fit under a pure p-hacking assumption, the estimates appear substantially more optimistic.

Under this model, evidence of p-hacking produces an excess of results just below p = .05, which are excluded from estimation. The resulting estimates suggest average power between 40% (EDR = .43) and 52% (ERR = .52), with relatively little heterogeneity. Nonsignificant results with z ≈ 1 are estimated to have average power of 46%, and significant results with z ≈ 4 have average power of 52%. If this model were correct, false positives would be rare and replication should be straightforward, especially with larger samples. The main difficulty with this interpretation is that preregistered replication studies consistently report average effect sizes near zero, directly contradicting these optimistic estimates (Dai et al., 2023).

Conclusion

So, is experimental social psychology a science? The most charitable answer is that it currently resembles a science with limited cumulative results in this domain. Meteorology is not a science because it acknowledges that weather varies; it is a science because it can predict weather with some reliability. Until social priming researchers can specify conditions under which priming effects reliably emerge in preregistered, confirmatory studies, the field lacks the predictive success expected of a mature empirical science.

Meanwhile willful ignorance and incompetence hamper progress towards this goal and undermine credible claims of psychology to be a science. Many psychology departments are being remained to have science in their name, but only acting in accordance with normative rules of science will make psychology a credible science.

Credible sciences also have a history of failures. Making mistakes is part of exploration. Covering them up is not. Meta-analyses of p-hacked studies without bias correction are misleading. Even worse are public significance statements directed at the general public rather than peers. The most honest public significance statement about social priming is “We fucked up. Sorry, we will do better in the future.”

Behavioral or social priming is the poster child of the replication crisis. Bargh declined Kahneman’s offer to rehabilitate it by showing that he could replicate his result. The same is true for other social psychologists who became famous for changing people’s behaviors without their knowledge / awareness.

While priming studies have largely disappeared from social psychology journals, the old studies still exist and have not been retracted although we know that they were obtained with unscientific methods that make it easy to present false evidence for false claims.

This allows unscientific meta-analysists to analyze these data and to continue to make claims that social priming is a real effect even in 2023 and even in a journal that is considered to be methodologically rigorous, although the name suggests otherwise (Psych Bull).

Dai, W., Yang, T., White, B. X., Palmer, R., Sanders, E. K., McDonald, J. A., Leung, M., & Albarracín, D. (2023). Priming behavior: A meta-analysis of the effects of behavioral and nonbehavioral primes on overt behavioral outcomes. Psychological Bulletin, 149(1-2), 67–98. https://doi-org.myaccess.library.utoronto.ca/10.1037/bul0000374

In the old days, the social power of censorship (peer-review) in scientific journals made it difficult to fight back against paradigm prisoners, who try to keep their little word of academia alive. Fortunately, consumers of scientific research now have options to ensure that they are not feeding their minds junk science.

I asked my ChatGPT (trained with discussions and information) to evaluate this article with a set of questions that anybody could ask an AI.

Critically evaluate this article.
Is the literature review accurate or misrepresent the broader literature
0 = totally false to 10 = totally accurate and consistent with current literature

Is this meta-analysis up to date or uses outdated methods
0 = totally outdated to 10 = totally up to date

Are the results interpreted correctly.
0 = totally misrepresents the results to 10 = totallly accurate

Integration with existing literature.
0 = not integrated at all, 10 = accurately interpreted in the context of broader literature

The scores are less important (as they would require comparison scores) than the reasons for the scores. Importantly, AI is neutral and more balanced than most humans, myself included, usually are.

Strengths

• The paper integrates its moderator findings into established theoretical disputes (perception–behavior link vs goal mediation), and it connects specific moderation patterns (e.g., goal value manipulations) to prior work and theoretical interpretations.
• It frames its contribution clearly as both (a) an expanded synthesis and (b) a mechanism-relevant test across moderators.

Limits

• Integration is strongest for the authors’ preferred theoretical framing; it is thinner on integrating the skeptical/critical meta-science side beyond noting that bias methods have “become ever more sophisticated” and providing the Lakens critique as a prompt. In other words, it engages critique more as a motivation for adding diagnostics than as a serious alternative interpretation of what the literature’s apparent “robustness” means. Priming_behavior_

I did ask a couple of follow up questions, mainly about the well-known problem that average effect sizes are meaningless when studies are heterogenous; priming sometimes works and sometimes it does not. To make priming research actually useful, we need to specify WHEN priming works. Priming MAY work or priming SOMETIMES works, is not a scientific finding.

On this point, the meta-analysis is as mute as most others are, but the paper will be cited as “priming works and has a moderate effect size.” Only psychologists believe that this is enough to defend priming against critics who say, “If priming works, why don’t you do a preregistered study with high power and show us that it works?”

ChatGPT Summary: This Meta-Analysis Tell Us When Priming Works?

The authors present an ambitious meta-analysis of priming effects on behavior and argue that replication failures can be reconciled with a “moderate” average effect size by appealing to heterogeneity and moderators. In principle, this is a legitimate defense: heterogeneous effects can exist even when many individual studies fail to replicate. In practice, however, the paper does not deliver what this defense requires.

Although substantial heterogeneity is documented, the moderator analyses do not clearly identify which studies work and which do not. Most examined moderators are weak, inconsistent, or explain only a small fraction of the variance. As a result, the analysis does not partition the literature into a subset of theoretically coherent, reliably effective studies versus a subset that fails. Without such discrimination, heterogeneity becomes descriptive rather than explanatory.

This creates a central tension in the paper’s conclusions. The authors argue for a nonzero average priming effect while simultaneously acknowledging widespread replication failures and publication bias. Yet they do not show that the moderators they test successfully predict when priming should occur. Consequently, the results do not support a practical or falsifiable claim about replicability. A new study cannot be classified, based on their findings, as likely to succeed or fail.

The strongest conclusion supported by the evidence is therefore modest: priming effects may exist under some conditions, but those conditions are not empirically established by the present meta-analysis. Claims of “moderate” effects should be interpreted as population averages over a poorly understood mixture of successful and unsuccessful studies, rather than as evidence that priming reliably works in practice.

In short, the paper shows that priming has not been decisively ruled out—but it does not show when, how, or how often it actually works.

POSTSCRIPT

PET allows for an effect size of d = 0.025. However, because this result rejects H0, d = 0, at the 5% level, the authors use the PEESE estimate that is always higher. If they had used alpha = .01 or a minim effect size of d = .1, PET would not have been rejected, and the average effect size estimate would be close to zero. Did the authors p-hack PET to be significant? It does not matter. The evidence is weak and the main problem remains. Heterogeneity without a clear moderator that explains when it works and when it does not. This is psycho-science, not real science.

PPS

Priming may work, but NOT when a study is preregistered. (hm?)

The File-Drawer Problem

A single study is rarely enough to provide sufficient evidence for a theoretically derived hypothesis. To make sense of inconsistent results across multiple studies, psychologists began to conduct meta-analysis. The key contribution of meta-analyses is that pooling evidence from multiple studies reduces sampling error and allows for more precise estimation of effect sizes.

The key problem of meta-analysis is the assumption that individual studies are an unbiased sample of all studies that were conducted. Selective publishing of statistically significant results in favor of a prediction leads to inflated effect size estimates. This problem has been dubbed the file drawer problem. Whereas significant results are submitted for publication, non-significant results are put into a file drawer.

Rosenthal (1979) pointed out that a literature consisting entirely of statistically significant findings could, in principle, reflect no true effects. However, such a scenario was often considered unlikely under the assumption of honest testing with a fixed Type I error rate, because studies without real effects produce a significant result only about 1 out of 20 times when the error rate is controlled with alpha = .05. In addition, Rosenthal proposed a statistic, fail-safe N, to evaluate this risk, and meta-analyses often found that fail-safe N was large enough to infer a real effect.

The assessment of the published literature in psychology shifted dramatically in the early 2010s. Critically, Simmons, Nelson, and Simonsohn (2011) showed with simulations that a few statistical tricks could increase the probability of significant results without real effects from 1:20 to nearly 1:2. Even consistent statistically significant results in several studies were no longer unlikely. Presenting 9 significant results would not require 180 studies, but only 18 (Bem, 2011), or even fewer with more extreme use of questionable statistical practices that later became known as p-hacking. This highly cited article created a crisis of confidence in single studies, and by extension also in meta-analytic findings.

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The False Positive Detection Problem

A few years later, Simonsohn, Nelson, and Simmons (2014) published a statistical method, p-curve, to probe the credibility of sets of statistically significant results, often drawn from meta-analyses. They referred to this method as a “key to the file drawer.” The analogy is potentially confusing. P-curve does not test whether publication bias exists, nor does it determine whether questionable statistical practices were used. It also does not estimate how many studies are in the proverbial file drawer. In fact, p-hacking implies that file drawers can be small, even if significant results are false positives. When p-hacking is present, the size of the file drawer is therefore no longer informative.

What p-curve does, and what it does better than fail-safe N, is to assess whether the observed set of statistically significant results is inconsistent with the hypothesis that all tested effects are exactly zero. Simonsohn et al. (2014) call this property evidential value. Formally, significance tests are applied to the distribution of significant p-values to evaluate the null hypothesis implied by this scenario. When this hypothesis can be rejected using conventional significance tests, the data are said to have evidential value. Later versions of p-curve also include stronger tests, but the underlying logic remains the same.

Equipped with a new diagnostic tool, psychologists had a different way to evaluate published studies. While p-curve still shares a limitation of significance testing—namely that it cannot provide affirmative evidence for the null hypothesis, such as the claim that all published significant results are false positives—it can nevertheless show that a set of studies fails to provide evidence against this extreme null hypothesis. Lack of evidence is still valuable information, especially when a set of statistically significant results appears to suggest strong support for a hypothesis, but this support is potentially driven by selective reporting or p-hacking rather than true effects.

P-Curve Coding

P-curve made it possible to evaluate the hypothesis that many, if not most (Ioannidis, 2005), published results are false positives. If this were the case, many p-curve meta-analyses of a specific hypothesis should be flat or left-skewed. In contrast, true hypotheses should produce right-skewed p-curves. Surprisingly, this simple approach to examine the false positive rate has not been systematically applied.

I conducted a review of p-curve articles to see what we have learned about false positives from a decade of p-curve analyses. The article introducing p-curve has been cited more than 1,000 times (WoS, December 30, 2025). I reviewed two samples of articles. First, I sampled the most highly cited articles. These articles are of interest because they may introduce many readers to p-curve, including readers who are not experts in meta-analysis. These articles are also more likely to report high-visibility results. The second set of articles focused on the most recent articles. The rationale is that more recent articles reflect current practice in how p-curve is used and how p-curve results are interpreted.

P-curve results were coded first in terms of evidential value (right-skewed vs. not right-skewed). The second classification concerned the proper interpretation of right-skewed p-curves. Correct interpretations were limited to claims about evidential value. However, some articles misinterpreted p-curve as a bias test and falsely inferred a low risk of bias from a p-curve with evidential value.

The coding scheme had three categories. First, articles that did not report a p-curve analysis were coded as irrelevant. Second, articles that reported a p-curve analysis and correctly limited discussion to evidential value were coded as correct. Third, some articles reported a p-curve analysis but made claims about bias, selection bias, or p-hacking that are invalid. Namely, these articles interpreted results showing evidential value to conclude that publication bias or p-hacking were not a concern. This conclusion is invalid because data can show evidential value while biases can still inflate effect size estimates simultaneously. These articles were coded as incorrect.

Articles were found using WebOfScience. Articles classified as editorial material were excluded. The list of coded articles and their coding is available on the Open Science Framework (OSF) project.

P-Curve Results

I coded 142 articles. A large number of them (k = 95; 67%) cited the p-curve article but did not report a p-curve analysis. An additional two articles stated that a p-curve analysis had been conducted but did not provide a clear description of the results. All 45 articles that reported a p-curve analysis found evidential value. Some of these articles showed flat p-curves for specific subsets of studies, but this pattern was attributed to theoretically meaningful moderators (e.g., Tucker-Drob & Bates, 2015). Importantly, none of the reviewed p-curve analyses suggested that all reported results were false positives.

To further probe this issue, I conducted an automated search of all 990 abstracts retrieved from Web of Science for references to p-curve results indicating no evidential value or flat p-curves. This search did not identify a single abstract reporting such a result.

In terms of interpretations, the results are also notable. More articles misrepresented p-curve as a bias test (k = 28) than correctly presented p-curve as a test of evidential value. Because p-curves were almost always right-skewed, these misinterpretations frequently led authors to infer a low risk of bias, which is not a valid inference from a right-skewed p-curve.

Once, p-curve was even used to discount evidence of bias obtained with other methods. For example, “Funnel plot analysis showed evidence of publication bias, but p-curve analysis suggested that our results could not be caused by selective reporting” (Goubran et al., 2025).

Discussion

Two influential theoretical articles raised concerns that many published rejections of null hypotheses could be false positive results (Ioannidis, 2005; Simmons et al., 2011). P-curve provides an opportunity to evaluate this prediction empirically, but the evidence obtained in p-curve meta-analyses has not been systematically examined. I found that p-curve results always showed evidential value. This finding is in stark contrast to scenarios that suggest the majority of statistically significant results are false (Ioannidis, 2005).

At the same time, p-curve is often misunderstood and misinterpreted as a bias test. This interpretation may lead to a false sense of the credibility of published results. Just as replication failures do not justify the inference that the original result was a false positive (Maxwell et al., 2006), evidential value does not imply that results can be replicated.

There are several possible explanations for the failure to find evidence of false positive results in meta-analyses. One explanation is that false positives are more likely to arise in individual studies than in meta-analyses, which require multiple studies testing the same hypothesis. Sustaining a literature of false positives would therefore require repeated and consistent use of extremely questionable research practices. Few researchers may be motivated to use extreme p-hacking repeatedly to force significant results in the absence of a real effect. Bem (2011) may represent an unusual case in that he appeared to be highly motivated to convince skeptical scientists of the existence of extrasensory perception and to present evidence that met prevailing methodological standards in experimental social psychology. More commonly, researchers may advance claims based on selective or suggestive evidence without attempting to build a cumulative evidential record.

Another explanation is that the statistical null-hypothesis is unlikely to be true (Cohen, 1994). What are the chances that an experimental manipulation has no effect whatsoever on behavior? Subliminal stimuli are often cited as candidates, but even in this literature concerns have been raised that effects may be driven by partial stimulus detection. In correlational research, it is even less likely that two variables have a true correlation of exactly zero. As a result, p-hacking may often inflate effect sizes rather than generate false positive results in the strict sense of rejecting a false null hypothesis.

The problem is when rejection of the nil-hypothesis is confused with credible evidence for a meaningful effect. For example, a p-curve analysis of ego depletion shows evidential value (Carter et al., 2019), but even the original authors were unable to replicate the effect (Vohs et al., 2019). This example illustrates that evidential value is a necessary but not sufficient condition for a credible science. Even if effect sizes are not exactly zero, they can be dramatically inflated. As p-curve is limited to the assessment of evidential value, other methods are required to (a) assess whether published results are biased by selection or p-hacking, (b) estimate population effect sizes while correcting for bias, and (c) estimate the false positive risk in heterogeneous meta-analyses, where a subset of statistically significant results may be false positives.

However, it is also possible that p-curve results are biased and provide spurious evidence of evidential value, that is, evidential value itself may constitute a meta-level false positive. In this case, p-curve would falsely reject the null hypothesis that all statistically significant results are false positives. One possible source of bias is that studies with stronger (but false) evidence may be more likely to be included in meta-analyses than studies with weaker (false) evidence. For example, some researchers may p-hack to more stringent thresholds (e.g., α = .01) or apply Bonferroni corrections, while standard meta-analytic coding practices may mask these selection processes. However, p-hacking of this kind would be expected to produce left-skewed or flat p-curves, such that explaining the near-absence of flat p-curves would require the additional assumption that extreme p-hacking is rare. At present, this possibility cannot be ruled out, but it appears unlikely to account for the overwhelming predominance of right-skewed p-curves.

A more plausible explanation is selective reporting of p-curve results. Because reporting p-curve analyses is optional, meta-analysts may be more likely to include p-curve results when they show evidential value and omit them when p-curves are flat or left-skewed. Evaluating this form of meta-analytic selection bias requires auditing meta-analyses that did not report p-curve results and applying the method retrospectively.

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Conclusion

The most important finding is that concerns about many false positive results in psychology journals are not based on empirical evidence. False positives in single studies are not important because no single study can serve as an empirical foundation for a theory. There is no evidence that entire literatures are just a collection of false positive results. This does not mean that published results are credible. Publication bias, inflation of effect sizes, low replicability, method factors in correlational studies, and lack of construct validation remains serious obstacles that have sometimes been overshadowed by concerns about false positive results. These issues deserve more attention in the future.

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Concerns about credibility are widespread, but they often do not clearly distinguish between different sciences. One problem is that it is difficult to compare sciences quantitatively. One way to do so is to examine the strength of empirical evidence. We cannot compare effect sizes across sciences, but we can compare how precise effect size estimates are and how often rejections of null hypotheses may be false.

The first “science-wide” study was based on empirical results in medicine (Jager & Leek, 2013). Their methods and results were challenged, and it took some time before alternative methods became available. A better method is z-curve (Bartos & Schimmack, 2022; Brunner & Schimmack, 2020). Z-curve has been mostly used in psychology. A comparison with medicine showed that clinical trials have less power, but report results more honestly than psycholgy, where focal tests confirm predicts with success rates over 90% (Schimmack, 2020; Schimmack & Bartos, 2023).

A recent article extracted confidence intervals from four epidemiology journals.

Ackley, S. F., Andrews, R. M., Seaman, C., Flanders, M., Chen, R., Wang, J., Lopes, G., Sims, K. D., Buto, P., Ferguson, E., Allen, I. E., & Glymour, M. M. (2025). Trends in the distribution of P values in epidemiology journals: A statistical, P-curve, and simulation study. American Journal of Epidemiology, 194(12), 3630–3639. https://doi.org/10.1093/aje/kwaf184

The authors were not aware of z-curve, but I was able to analyze their shared data. I examined trends over time and found no evidence that z-curve parameters correlated with publication year. Thus, the results are representative of the literature. An initial analysis with standard z-curve showed no evidence of selection bias. Therefore, I fitted the full data, including non-significant results.

The key findings are: (a) The observed and expected discovery rates are 91%. This means that 91% of the results are significant, but the reason is not selection bias – as it is often in psycholoy – but high power to reject false null hypotheses; (b) a very low false positive risk even with alpha = .05, and a high probability that an exact replication study with a new sample from the same population would produce a significant result again. However, there is some evidence of p-hacking. That is there are more just significant results (2 to 2.4) than the model predicts, Excessive Just Significance Test, p = .0008. Visual inspection of the plot shows, however, that the effect size is small, observed 0.25%, expected 0.24%, and that statistical significance reflects mainly the large sample size.

In short, this is a healthy literature that instills confidence in epidemiological research. The reason is that epidemiological studies typically have large sample sizes and aim for precise effect size estimation. With this goal in mind, studies have high power to reject the null hypothesis of no effect, if only because doing so is not very informative. In contrast, psychologists often use small samples that are sometimes not even large enough to test a null hypothesis properly. Comparing epidemiology with psychology is therefore a bit like comparing apples and oranges, but this false comparison is often made when science as a whole is evaluated. In reality, different sciences face different problems. Low power and replicability are a problem for sciences that invest few resources in many studies, such as psychology. We cannot generalize from replication failures in these sciences to other sciences.

For psychology, effect sizes estimation mostly remains a scientific utopia, but the z-curve of epidemiology shows what that utopia looks like.