Update: March 14, 2021
Jerry Brunner and I developed a method to estimate average power of studies while taking selection for significance into account. We validated our method with simulation studies. We also show that other methods that are already in use for effect size estimation, like p-curve, produce biased (inflated) estimates. You might think that an article that relies on validated simulations to improve on an existing method, z-curve is better than p-curve, would be published, especially be a journal that was created to improve / advance psychological science. However, this blog post shows that AMPPS works like any other traditional, for-profit, behind pay-wall journal. Normally, you would not be able to see the editorial decision letter or know that an author of the inferior p-curve method provided a biased review. But, here you can see how traditional publishing works (or doesn’t work).
Meanwhile the article has been published in the journal Meta-Psychology, a journal without fees for authors, open access to articles, and transparent peer-reviews.
The article: https://open.lnu.se/index.php/metapsychology/article/view/874
The peer-review report can be found on OSF: https://osf.io/peumw/
Also, three years after the p-curve authors have been alerted to the fact that their method can provide biased estimates, they have not modified their app or posted a statement that alerts readers to this problem. This is how even meta-scientists operate.
Dear Dr. Schimmack:
Thank you for submitting your manuscript (AMPPS-17-0114) entitled “Z-Curve: A Method for the Estimating Replicability Based on Test Statistics in Original Studies” to Advances in Methods and Practices in Psychological Science (AMPPS). First, my apologies for the overly long review process. I initially struggled to find reviewers for the paper and I also had to wait for the final review. In the end, I received guidance from three expert reviewers whose comments appear at the end of this message.
Reviewers 1 and 2 chose to remain anonymous and Reviewer 3 is Leif Nelson (signed review). Reviewers 1 and 2 were both strongly negative and recommended rejection. Nelson was more positive about the goals of the paper and approach, although he wasn’t entirely convinced by the approach and evidence. I read the paper independently of the reviews, both before sending it out and again before reading the reviews (given that it had been a while). My take was largely consistent with that of the reviewers.
Although the issue of estimating replicability from published results is an important one, I was less convinced about the method and felt that the paper does not do enough to define the approach precisely, and it did not adequately demonstrate its benefits and limits relative to other meta-analytic bias correction techniques. Based on the comments of the reviewers and my independent evaluation, I found these issues to be substantial enough that I have decided to decline the manuscript.
The reviews are extensive and thoughtful, and I won’t rehash all of the details in my letter. I would like to highlight what I see as the key issues, but many of the other comments are important and substantive. I hope you will find the comments useful as you continue to develop this approach (which I do think is a worthwhile enterprise).
All three reviews raised concerns about the clarity of the paper and the figures as well as the lack of grounding for a number of strong claims and conclusions (they each quote examples). They also note the lack of specificity for some of the simulations and question the datasets used for the analyses.
I agreed that the use of some of the existing data sets (e.g., the scraped data, the Cuddy data, perhaps the Motyl data) are not ideal ways to demonstrate the usefulness of this tool. Simulations in which you know and can specify the ground truth seem more helpful in demonstrating the advantages and constraints of this approach.
Reviewers 1 and 2 both questioned the goal of estimating average power. Reviewer 2 presents the strongest case against doing so. Namely, average power is a weird quantity to estimate in light of a) decades of research on meta-analytic approaches to estimating the average effect size in the face of selection, and b) the fact that average power is a transformation of effect size. To demonstrate that Z-curve is a valid measure and an improvement over existing approaches, it seems critical to test it against other established meta-analytic models.
p-curve is relatively new, and as reviewer 2 notes, it has not been firmly established as superior to other more formal meta-analytic approaches (it might well be better in some contexts and worse in others). When presenting a new method like Z-curve, it’s is important to establish it against well-grounded methods or at least to demonstrate how accurate, precise, and biased it is under a range of realistic scenarios. In the context of this broader literature on bias correction, the comparison only to p-curve seems narrow, and a stronger case would involve comparing the ability of Z-curve to recover average effect size against other models of bias correction (or power if you want to adapt them to do that).
[FYI: p-curve is the only other method that aims to estimate average power of studies selected for significance. Other meta-analytic tools aim to estimate effect sizes, which are related to power but not identical. ]
Nelson notes that other analyses show p-curve to be robust to heterogeneity and argues that you need to more clearly specify why and when Z curve does better or worse. I would take that as a constructive suggestion that is worth pursuing. (e.g., he and the other reviewers are right that you need to provide more specificity about the nature of the heterogeneity your modeling.).
I thought Nelson’s suggestions for ways to explain the discrepant results of these two approaches were constructive, and they might help to explain when each approach does better, which would be a useful contribution. Just to be clear, I know that the datacolada post that Nelson cites was posted after your paper was submitted and I’m not factoring your paper’s failure to anticipate it into my decision (after all, Bem was wrong).
[That blog post was posted after I shared our manuscript with Uri and tried to get him to comment on z-curve. In a long email exchange he came up with scenarios in which p-curve did better,but never challenged the results of my simulations that it performs a lot worse when there is heterogeneity. To refer to this self-serving blog post as a reason for rejection is problematic at best, especially if the simulation results in the manuscript are ignored.
Like Reviewer 2 and Nelson, I was troubled by the lack of a data model for Z curve (presented around page 11-12). As best I can tell, it is a weighted average of 7 standard normal curves with different means. I could see that approach being useful, and it might well turn out to be optimal for some range of cases, but it seems arbitrary and isn’t suitably justified. Why 7? Why those 7? Is there some importance to those choices?
The data model (never heard the term, model) was specified and it is so simple that the editorial letter even characterizes it correctly. The observed density distribution is modeled with weighted averages of the density distributions of 7 standard normal distributions and yes 7 is arbitrary because it has very little influence on the results.
Do they reflect some underlying principle or are they a means to an end? If the goal is to estimate only the end output from these weights, how do we know that those are the right weights to use?
Because the simulation results show that the model recovers the simulated average power correctly within 3% points?
If the discrete values themselves are motivated by a model, then the fact that the weight estimates for each component are not accurate even with k=10000 seems worrisome.
No it is not worrisome because the end goal is the average, not the individual weights.
If they aren’t motivated by a more formal model, how were they selected and what aspects of the data do they capture? Similarly, doesn’t using absolute value mean that your model can’t handle sign errors for significant results? And, how are your results affected by an arbitrary ceiling at z=6?
There are no sign errors in analyses of significant results that cover different research questions. Heck, there is not even a reasonable way to speak about signs. Is neuroticism a negative predictor of wellbeing or is emotional stabilty a positive predictor of wellbeing?
Finally, the paper comments near the end that this approach works well if k=100, but that doesn’t inform the reader about whether it works for k=15 or k=30 as would be common for meta-analysis in psychology.
The editor doesn’t even seem to understand that this method is not intended to be used for a classic effect size meta-analysis. We do have statistical methods for that. Believe me I know that. But how would we apply these methods to estimate the replicability of social psychology? And why would we use k = 30 to do so, when we can use k = 1,000?
To show that this approach is useful in practice, it would be good to show how it fares with sets of results that are more typical in scale in psychology. What are the limits of its usefulness? That could be demonstrated more fully with simulations in which the ground truth is known.
No bias correction method that relies on only significant results provides meaningful results with k = 30. We provide 95%CI and they are huge with k = 30.
I know you worked hard on the preparation of this manuscript, and that you will be disappointed by this outcome. I hope that you will find the reviewer comments helpful in further developing this work and that the outcome for this submission will not discourage you from submitting future manuscripts to AMPPS.
Daniel J. Simons, Editor
Advances in Methods and Practices in Psychological Science (AMPPS) Psychology
Unfortunately, I don’t think the editor worked hard on reading the manuscript and missed the main point of the contribution. So, no I am not planning on wasting more time on sending my best work to this journal. I had hopes that AMPPS was serious about improving psychology as a science. Now I know better. I will also no longer review for your journal. Good luck with your efforts to do actual replication studies. I will look elsewhere to publish my work that makes original research more credible to start with.
The authors of this manuscript introduce a new statistical method, the z-curve, for estimating the average replicability of empirical studies. The authors evaluate the method via simulation methods and via select empirical examples; they also compare it to an alternative approach (p-curve). The authors conclude that the z-curve approach works well, and that it may be superior to the p-curve in cases where there is substantial heterogeneity in the effect sizes of the studies being examined. They also conclude, based on applying the z-curve to specific cases, that the average power of studies in some domains (e.g., power posing research and social psychology) is low.
One of the strengths of this manuscript is that it addresses an important issue: How can we evaluate the replicability of findings reported in the literature based on properties inherent to the studies (or their findings) themselves? In addition, the manuscript approaches the issue with a variety of demonstrations, including simulated data, studies based on power posing, scraped statistics from psychology journals, and social psychological studies.
After reading the manuscript carefully, however, I’m not sure I understand how the z-curve works or how it is supposed to solve potential problems faced by other approaches for evaluating the power of studies published in the empirical literature.
That is too bad. We provided detailed annotated R-Code to make it possible for quantitative psychologists to understand how z-curve works. It is unfortunate that you were not able to understand the code. We would have been happy to answer questions.
I realize the authors have included links to more technical discussions of the z-curve on their websites, but I think a manuscript like this should be self-contained–especially when it is billed as an effort “to introduce and evaluate a new statistical method” (p. 25, line 34).
We think that extensive code is better provided in a supplement. However, this is really an editorial question and not a comment on the quality or originality of our work.
Some additional comments, questions, and suggestions:
1. One of my concerns is that the approach appears to be based on using “observed power” (or observed effect sizes) as the basis for the calculations. And, although the authors are aware of the problems with this (e.g., published effect sizes are over-estimates of true effect sizes; p. 9), they seem content with using observed effect sizes when multiple effect sizes from diverse studies are considered. I don’t understand how averaging values that are over-estimates of true values can lead to anything other than an inflated average. Perhaps this can be explained better.
Again, we are sorry that you did not understand how our method achieves this goal, but that is surely not a reason to recommend rejection
2. Figure 2 is not clear. What is varying on the x-axis? Why is there a Microsoft-style spelling error highlighted in the graph?
The Figure was added after an exchange with Uri Simonsohn and reproduces the simulation that they did for effect sizes (see text). The x-axis shows d-values.
3. Figure 4 shows a z-curve for power posing research. But the content of the graph isn’t explained. What does the gray, dotted line represent? What does the solid blue line represent? (Is it a smoothed density curve?) What do the hashed red vertical lines represent? In short, without guidance, this graph is impossible to understand.
Thank you for your suggestion. We will revise the manuscript to make it easier to read the figures.
4. I’m confused on how Figure 2 is relevant to the discussion (see p. 19, line 22)
Again. We are sorry about the confusion that we caused. The Figure shows that p-curve overestimates power in some scenarios (d = .8, SD = .2) which was not apparent when Simonsohn did these simulation to estimate effect sizes.
5. Some claims are made without any explanation or rationale. For example, on page 19 the authors write “Random sampling error cannot produce this drop” when commenting on the distribution of z-scores in the power posing data. But no explanation is offered for how this conclusion is reached.
Random sampling error of z-scores is one. So, we should see a lot of values next to the mode of a distribution. A steep drop cannot be produced by random sampling error. The same observation has been made repeatedly about a string of just significant p-values. If you can get .04., .03, .02, again and again, why do you not get .06 or .11?
6. I assume the authors are re-analyzing the data collected by Motyl and colleagues for Demonstration 3? This isn’t stated explicitly; one has to read between the lines to reach this conclusion.
You read correctly between the lines
7. Figure 6 contains text which states that the estimated replicability is 67%. But the narrative states that the estimated replicability using the z-curve approach is 46% (p. 24, line 8). Is the figure using a different method than the z-curve method?
This is a real problem. This was the wrong Figure. Thank you for pointing it out. The estimate in the text is correct.
8. p. 25. Unclear why Figure 4 is being referenced here.
Another typo. Thanks for pointing it out.
9. The authors write that “a study with 80% power is expected to produce 4 out of 5 significant results in the long run.” (p. 6). This is only true when the null hypothesis is false. I assume the authors know this, but it would be helpful to be precise when describing concepts that most psychologists don’t “really” understand.
If a study has 80% power it is assumed that the null-hypothesis is false. A study where the null-hypothesis is true has a power of alpha to produce significant results.
10. I am not sure I understand the authors’ claim that, “once we take replicability into account, the distinction between false positives and true positives with low power becomes meaningless.” (p. 7).
We are saying in the article that there is no practical difference between a study with power = alpha (5%) where the null-hypothesis is true and a study with very low power (6%) where the null-hypothesis is false. Maybe it helps to think about effect sizes. d = 0 means null is true and power is 5% and d = 0.000000000000001 means null-hypothesis is false and power is 5.000000001%. In terms o f the probability to replicate a significant result both studies have a very low probability of doing so.
11. With respect to the second demonstration: The authors should provide a stronger justification for examining all reported test statistics. It seems that the z-curve’s development is mostly motivated by debates concerning the on-going replication crisis. Presumably, that crisis concerns the evaluation of specific hypotheses in the literature (e.g., power posing effects of hormone levels) and not a hodge-podge of various test results that could be relevant to manipulation checks, age differences, etc. I realize it requires more work to select the tests that are actually relevant to each research article than to scrape all statistics robotically from a manuscript, but, without knowing whether the tests are “relevant” or not, it seems pointless to analyze them and draw conclusions about them.
This is a criticism of one dataset, not a criticism of the method.
12. Some of the conclusions that the authors research, such as “our results suggest that the majority of studies in psychology fail to meet the minimum standard of a good study . . . and even more studies fail to meet the well-known and accepted norm that studies should have 80% power” have been reached by other authors too.
But what methodology did these authors used to come to this conclusion? Did they validate their method with simulation studies?
This leads me to wonder whether the z-curve approach represents an incremental advance over other approaches. (I’m nitpicking when I say this, of course. But, ultimately, the “true power” of a collection of studies is not really a “thing.”
What does that mean the true power of studies is not a thing. Researchers conduct significance tests (many) and see whether they get a publishable significant result. The average percentage of times they get a significant result is the true average power of the population of statistical tests that are being conducted. Of course, we can only estimate this true value, but who says that other estimates that we use everyday are any better than the z-curve estimates?
It is a useful fiction, of course, but getting a more precise estimate of it might be overkill.)
Sure let’s not get to precise. Why don’t we settle for 50% +/- 50% and call it a day?
Perhaps the authors can provide a stronger justification for the need of highly precise, but non-transparent, methods for estimating power in published research?
Just because you don’t understand the method doesn’t mean it is not transparent and maybe it could be useful to know that social psychologists conduct studies with 30% power and only publish results that fit their theories and got significant with the help of luck? Maybe we have had 6 years of talk about a crisis without any data except the OSC results in 2015 that are limited to 2008 and three journals. But maybe we just don’t care because it is 2018 and it is time to get on with business as usual. Glad you were able to review for a new journal that was intended to Advance Methods and Practices in Psychological Science. Clearly estimating the typical power of studies in psychology is not important for this goal in your opinion. Again sorry for submitting such a difficult manuscript and wasting your time.
The authors present a new methodology (“z-curve”) that purports to estimate the average of the power of a set of studied included in a meta-analysis which is subject to publication bias (i.e., statistically significant studies are over-represented among the set meta-analyzed). At present, the manuscript is not suitable for publication largely for three major reasons.
 Average Power: The authors propose to estimate the average power of the set of prior historical studies included in a meta-analysis. This is a strange quantity: meta-analytic research has for decades focused on estimating effect sizes. Why are the authors proposing this novel quantity? This needs ample justification. I for one see no reason why I would be interested in such a quantity (for the record, I do not believe it says much at all about replicability).
Why three reasons, if the first reason is that we are doing something silly. Who gives a fuck about power of studies. Clearly knowing how powerful studies are is as irrelevant as knowing the number of potholes in Toronto. Thank you for your opinion that unfortunately was shared by the editor and mostly the first reviewer.
There is another reason why this quantity is strange, namely it is redundant. In particular, under a homogeneous effect size, average power is a simple transformation of the effect size; under heterogeneous effect sizes, it is a simple transformation of the effect size distribution (if normality is assumed for the effect size distribution, then a simple transformation of the average effect size and the heterogeneity variance parameter; if a more complicated mixture distribution is assumed as here then a somewhat more complicated transformation). So, since it is just a transformation, why not stick with what meta-analysts have focused on for decades!
You should have stopped when things were going good. Now you are making silly comments that show your prejudice and ignorance. The whole point of the paper is to present a method that estimate average power when there is heterogeneity (if this is too difficult for you, let’s call it variability or even better, you know, bro, power is not always the same in each study). If you missed this, you clearly didn’t read the manuscript for more than two minutes. So, your clever remark about redundancy is just a waste of my time and the time of readers of this blog because things are no longer so simple when there is heterogeneity. But may be you even know this but just wanted to be a smart ass.
 No Data Model / Likelihood: On pages 10-13, the authors heuristically propose a model but never write down the formal data model or likelihood. This is simply unacceptable in a methods paper: we need to know what assumptions your model is making about the observed data!
We provided r-code that not only makes it clear how z-curve works but also was available for reviewers to test it. The assumptions are made clear and are simple. This is not some fancy Bayesian model with 20 unproven priors. We simply estimate a single population parameter from the observed distribution of z-scores and we make this pretty clear. It is simple, makes no assumptions, and it works. Take that!
Further, what are the model parameters? It is unclear whether they are mixture weights as well as means, just mixture weights, etc. Further, if just the weights and your setting the means to 0, 1, …, 6 is not just an example but embedded in your method, this is sheer ad hockery.
Again, it works. What is your problem?
It is quite clear from your example (Page 12-13) the model cannot recover the weights correctly even with 10,000 (whoa!) studies! This is not good. I realize your interest is on the average power that comes out of the model and not the weights themselves (these are a means to an end) but I would nonetheless be highly concerned—especially as 20-100 studies would be much more common than 10,000.
Unlike some statisticians we do not pretend that we can estimate something that cannot be estimated without making strong and unproven assumptions. We are content with estimating what we can estimate and that is average power, which of course, you think is useless. If average power is useless, why would it be better if we could estimate the weights?
 Model Validation / Comparison: The authors validate their z-curve by comparing it to an ad hoc improvised method known as the p-curve (“p-Curve and effect size”, Perspectives on Psychological Science, 2014). The p-curve method was designed to estimate effect sizes (as per the title of the paper) and is known to perform extremely poorly at estimating at this task (particularly under effect size heterogeneity); there is no work validating how well it performs at estimating this rather curious average power quantity (but likely it would do poorly given that it is poor at estimating effect sizes and average power is a transformation of the effect size). Thus, knowing the z-curve performs better than the p-curve at estimating average power tells me next to nothing: you cannot validate your model against a model that has no known validation properties! Please find a compelling way to validate your model estimates (some suggested in the paragraphs below) whether that is via theoretical results, comparison to other models known to perform well, etc. etc.
No we are not validating z-curve with p-curve. We are validating z-curve with simulation studies that show z-curve produces good estimates of simulated true power. We only included p-curve to show that this method produces biased estimates when there is considerable variability in power.
At the same time, we disagree with the claim that p-curve is not a good tool to estimate average effect sizes from a set of studies that are selected for significance. It is actually surprisingly good at estimating the average effect size for the set of studies that were selected for significance (as is puniform).
It is not a good tool to estimate the effect size for the population of studies before selection for significance, but this is irrelevant in this context because we focus on replicability which implies that an original study produced a significant result and we want to know how likely it is that a replication study will produce a significant result again.
Relatedly, the results in Table 1 are completely inaccessible. I have no idea what you are presenting here and this was not made clear either in the table caption or in the main text. Here is what we would need to see at minimum to understand how well the approach performs—at least in an absolute sense.
[It shows the estimates (mean, SD) by the various models for our 3 x 3 design of the simulation study. But who cares, the objective is useless so you probably spend 5 seconds trying to understand the Table.]
First, and least important, we need results around bias: what is the bias in each of the simulation scenarios (these are implicitly in the Table 1 results I believe)? However, we also need a measure of accuracy, say RMSE, a metric the authors should definitely include for each simulation setting. Finally, we need to know something about standard errors or confidence intervals so we can know the precision of individual estimates. What would be nice to report is the coverage percentage of your 95% confidence intervals and the average width of these intervals in each simulation setting.
There are many ways to present results about accuracy. Too bad we didn’t pick the right way, but would it matter to you? You don’t really think it is useful anyways.
This would allow us to, if not compare methods in a relative way, to get an absolute assessment of model performance. If, for example, in some simulation you have a bias of 1% and an RMSE of 3% and coverage percentage of 94% and average width of 12% you would seem to be doing well on all metrics*; on the other hand, if you have a bias of 1% and an RMSE of 15% and coverage percentage of 82% and average width of 56%, you would seem to be doing poorly on all metrics but bias (this is especially the case for RMSE and average width bc average power is bounded between 0% and 100%).
* Of course, doing well versus poorly is in the eye of the beholder and for the purposes at hand, but I have tried to use illustrative values for the various metrics that for almost all tasks at hand would be good / poor performance.
For this reason, we presented the Figure that showed how often the estimates were outside +/- 10%, where we think estimates of power do not need to be more precise than that. No need to make a big deal out of 33% vs. 38% power, but 30% vs. 80% matters.
I have many additional comments. These are not necessarily minor at all (some are; some aren’t) but they are minor relative to the above three:
[a] Page 4: a prior effect size: You dismiss these hastily which is a shame. You should give them more treatment, and especially discuss the compelling use of them by Gelman and Carlin here:
This paper is absolutely irrelevant for the purpose of z-curve to estimate the actual power that researchers achieve in their studies.
[b] Page 5: What does “same result” and “successful replication” mean? You later define this in terms of statistical significance. This is obviously a dreadful definition as it is subject to all the dichotomization issues intrinsic to the outmoded null hypothesis significance paradigm. You should not rely on dichotomization and NHST so strongly.
What is obvious to you, is not the scientific consensus. The most widely used criterion for a succesful replicaiton study is to get a significant result again. Of course, we could settle for getting the same sign again and a 50% type-I error probability, but hey, as a reviewer you get to say whatever you want without accountability.
Further, throughout please replace “significant” by “statistically significant” and related terms when it is the latter you mean.
[c] Page 6: Your discussion regarding if studies had 80% then up to 80% of results would be successful is not quite right: this would depend on the prior probability of “non-null” studies.
[that is why we wrote UP TO]
[d] Page 7: I do not think 50% power is at all “good”. I would be appalled in fact to trust my scientific results to a mere coin toss. You should drop this or justify why coin tosses are the way we should be doing science.
We didn’t say it is all good. We used it as a minimum, less than that is all bad, but that doesn’t mean 50% is all good. But hey, you don’t care anyways. so what the heck.
[e] Page 10: Taking absolute values of z-statistics seems wrong as the sign provides information about the sign of the effect. Why do you do this?
It is only wrong if you are thinking about a meta-analysis of studies that test the same hypothesis. However, if I want to examine the replicability of more than one specific hypothesis all results have to be coded so that a significant results implies support for the hypothesis in the direction of significance.
[f] Page 13 and throughout: There are ample references to working papers and blog posts in this paper. That really is not going to cut it. Peer review is far from perfect but these cited works do not even reach that low bar.
Well better than quoting hearsay rumors form blog posts that coding in some dataset is debatable in a peer review of a methods paper.
[g] Page 16: What was the “skewed distribution”? More details about this and all simulation settings are necessary. You need to be explicit about what you are doing so readers can evaluate it.
We provided the r-code to recreate the distributions or change them. It doesn’t matter. The conclusions remain the same.
[h] Page 15, Figure 2: Why plot median and no mean? Where are SEs or CIs on this figure?
Why do you need a CI or SE for simulations and what do you need to see that there is a difference between 0 and 80%?
[i] Page 14: p-curve does NOT provide good estimates of effect sizes!
Wrong. You don’t know what you are talking about. It does provide a good estimate of average effect sizes for the set of studies selected for significance, which is the relevant set here.
[j] You find p-curve is biased upwards for average power under heterogeneity; this seems to follow directly from the fact that it is biased upwards for effect size under heterogeneity (“Adjusting for Publication Bias in Meta-analysis”, Perspectives on Psychological Science, 2016) and the simply mapping between effect size and average power discussed above.
Wrong again. You are confusing estimates of average effect size for the studies before selection and after selection for significance.
[k] Page 20: Can z-curve estimate heterogeneity (the answer is yes)? You should probably provide such estimates.
We do not claim that z-curve estimates heterogeneity. Maybe some misunderstanding.
[l] Page 21-23: I don’t think the concept of the “replicability of all of psychology” is at all meaningful*. You are mixing apples and oranges in terms of areas studies as well as in terms of tests (focal tests vs manipulation checks). I would entirely cut this.
Of course, we can look for moderators but that is not helpful to you because you don’t think the concept of power is useful.
* Even if it were, it seems completely implausible that the way to estimate it would be to combine all the studies in a single meta-analysis as here.
[m] Page 23-25: I also don’t think the concept of the “replicability of all of social psychology” is at all meaningful. Note also there has been much dispute about the Motyl coding of the data so it is not necessarily reliable.
Of course you don’t, but why should I care about your personal preferences.
Further, why do you exclude large sample, large F, and large df1 studies? This seems unjustified.
They are not representative, but it doesn’t make a difference.
[n] Page 25: You write “47% average power implies that most published results are not false positives because we would expect 52.5% replicability if 50% of studies were false positives and the other 50% of studies had 100% power.” No, I think this will depend on the prior probability.
Wrong again. If 50% of studies were false positives, the power estimate would be 5%. To get an average of 50%, and the other studies have the maximum of 100% power, we would get a clearly visible bimodal distribution of z-scores and we would get an average estimate of p(H0) * 2.5 + (1-p(H0) * 100. You are a smart boy (sorry assuming this is a dick), you figure it out.
[o] Page 25: What are the analogous z-curve results if those extreme outliers are excluded? You give them for p-curve but not z-curve.
We provided that information, but you would need to care to look for them.
[p] Page 27: You say the z-curve limitations are not a problem when there are 100 or more studies and some heterogeneity. The latter is fine to assume as heterogeneity is rife in psychological research but seldom do we have 100+ studies. Usually 100 is an upper bound so this poses problems for your method.
It doesn’t mean our method doesn’t work with smaller N. Moreover, the goal is not to conduct effect size meta-analysis, but apparently you missed that because you don’t really care about the main objective to estimate replicability. Not sure why you agreed to review a paper that is titled “A method for estimating replicability?”
Final comment: Thanks for nothing.
This review was conducted by Leif Nelson
[Thank you for signing your review.]
Let me begin by apologizing for the delay in my review; the process has been delayed because of me and not anyone else in the review team.
Not sure why the editor waited for your review. Could have rejected it after reading the first two reviews that the whole objective, which you and I think is meaningful, is irrelevant for advancing psychological science. Sorry for the unnecessary trouble.
Part of the delay was because I spent a long time working on the review (as witnessed by the cumbersome length of this document). The paper is dense, makes strong claims, and is necessarily technical; evaluating it is a challenge.
I commend the authors for developing a new statistical tool for such an important topic. The assessment of published evidence has always been a crucial topic, but in the midst of the current methodological renaissance, it has gotten a substantial spotlight.
Furthermore, the authors are technically competent and the paper articulates a clear thesis. A new and effective tool for identifying the underlying power of studies could certainly be useful, and though I necessarily have a positive view of p-curve, I am open to the idea that a new tool could be even better.
Ok, enough with the politeness. Let’s get to it.
I am not convinced that Z-curve is that tool. To be clear, it might be, but this paper does not convince me of that.
As expected,…. p < .01. So let’s hear why the simulation results and the demonstration of inflated estimates in real datasets do not convince you.
I have a list of concerns, but a quick summary might save someone from the long slog through the 2500 words that follow:
- The authors claim that, relative to Z-curve, p-curve fails under heterogeneity and do not report, comment on, or explain analyses showing exactly the opposite of that assertion.
Wow. let me parse this sentence. The authors claim p-curve fails under heterogeneity (yes) and do not report … analyses showing … the opposite of that assertion.
Yes, that is correct. We do not show results opposite to our assertion. We show results that confirm our assertion in Figure 1 and 2. We show in simulations with R-code that we provided and you could have used to run your own simulations that z-curve provides very good estimates of average power when there is heterogeneity and that p-curve tends to overestimate average power. That is the key point of this paper. Now how much time did you spend on this review, exactly?
The authors do show that Z-curve gives better average estimates under certain circumstances, but they neither explain why, nor clarify what those circumstances look like in some easy to understand way, nor argue that those circumstances are representative of published results.
Our understanding was that technical details are handled in the supplement that we provided. The editor asked us to supply R-code again for a reviewer but it is not clear to us which reviewer actually used the provided R-code to answer technical questions like this. The main point is made clear in the paper. When the true power (or z-values) varies across studies, p-curve tends to overestimate. Not sure the claims of being open are very credible if this main point is ignored.
3. They attempt to demonstrate the validity of the Z-curve with three sets of clearly invalid data.
No. we do not attempt to validate z-curve with real datasets. That would imply that we already know the average power in real data, which we do not. We used simulations to validate z-cure and to show that p-curve estimates are biased. We used real data only to show that the differences in estimates have real world implications. For example, when we use the Motyl et al. (JSPSP) data to examine replicability, z-curve gives a reasonable estimate of 46% (in line with the reported R-Index estimates in the JPSP article), while p-curve gives an estimate of 72% power. This is not a demonstration of validity, it is a demonstration that p-curve would overestimate replicability of social psychological findings in a way that most readers would consider practically meaningful. ]
I think that any one of those would make me an overall negative evaluator; the combination only more so. Despite that, I could see a version which clarified the “heterogeneity” differences, acknowledged the many circumstances where Z-curve is less accurate than p-curve, and pointed out why Z-curve performs better under certain circumstances. Those might not be easy adjustments, but they are possible, and I think that these authors could be the right people to do it. (the demonstrations should simply be removed, or if the authors are motivated, replaced with valid sets).
We already point out when p-curve does better. When there is minimal variability or actually identical power, precision of p-curve is 2-3% better.
Brief elaboration on the first point: In the initial description of p-curve the authors seem to imply that it should/does/might have “problems when the true power is heterogeneous”. I suppose that is an empirical question, but it one that has been answered. In the original paper, Simonsohn et al. report results showing how p-curve behaves under some types of heterogeneity. Furthermore, and more recently, we have reported how p-curve responds under other different and severe forms of heterogeneity (dataclolada.org/67). Across all of those simulations, p-curve does indeed seem to perform fine. If the authors want to claim that it doesn’t perform well enough (with some quantifiable statement about what that means), or perhaps that there are some special conditions in which it performs worse, that would be entirely reasonable to articulate. However, to say “the robustness of p-curve has not been tested” is not even slightly accurate and quite misleading.
These are totally bogus and cheery-picked simulations that were conducted after I shared a preprint of this manuscript with Uri. I don’t agree with Reviewer 2 that we shouldn’t use blogs, but the content of the blog post needs to be accurate and scientific. The simulations in this blog post are not. The variation of power is very small. In contrast, we examine p-curve and z-curve in a fair comparison with varying amounts of heterogeneity that is found in real data sets. In this simulations p-curve again does slightly better when there is no heterogeneity, but it does a lot worse when there is considerable variability.
To ignore the results in the manuscript and to claim that the blog post shows something different is not scientific. It is pure politics. The good news is that simulation studies have a real truth and the truth is that when you simulate large variability in power, p-curve starts overestimating average power. We explain that this is due to the use of a single parameter model that cannot model heterogeneity. If we limit z-curve to a single parameter it has the same problem. The novel contribution of z-curve is to use multiple (3 or 7 doesn’t matter much) parameters to model heterogeneity. Not surprisingly, a model that is more consistent with the data produces better estimates.
Brief elaboration on the second point: The paper claims (and shows) that p-curve performs worse than Z-curve with more heterogeneity. DataColada claims (and shows) that p-curve performs better than Z-curve with more heterogeneity.
p-curve does not perform better with more heterogeneity. I had a two-week email exchange with Uri when he came up with simulations that showed better performance of p-curve. For example, transformation to z-scores is an approximation and when you use t-values with small N (all studies have N = 20), the approximation leads to suboptimal estimates. Also smaller k is an issue because z-curve estimates density distributions. So, I am well aware of limited specialized situations where p-curve can do better by up to 10% points, but that doesn’t change the fact that it does a lot worse when p-curve is applied to real heterogeneous data like I have been analyzing for years (ego-depletion replicability report, Motyl focal hpyothesis tests, etc. etc.).
I doubt neither set of simulations. That means that the difference – barring an error or similar – must lie in the operational definition of “heterogeneity.” Although I have a natural bias in interpretation (I assisted in the process of generating different versions of heterogeneity to then be tested for the DataColada post), I accept that the Z-curve authors may have entirely valid thinking here as well. So a few suggestions: 1. Since there is apparently some disagreement about how to operationalize heterogeneity, I would recommend not talking about it as a single monolithic construct.
How is variability in true power not a single construct. We have a parameter and it can vary from alpha to 1. Or we have a population effect size and a specific amount of sampling error and that gives us a ratio that reflects the deviation of a test statistic from 0. I understand the aim of saving p-curve, but in the end p-curve in its current form is unable to handle larger amounts of heterogeneity. You provide no evidence to the contrary.
Instead clarify exactly how it will be operationalized and tested and then talk about those. 2. When running simulations, rather than only reporting the variance or the skewness, simply show the distribution of power in the studies being submitted to Z-curve (as in DataColada). Those distributions, at the end of the day, will convey what exactly Z-curve (or p-curve) is estimating. 3. To the extent possible, figure out why the two differ. What are the cases where one fails and the other succeeds? It is neither informative (nor accurate) to describe Z-curve as simply “better”. If it were better in every situation then I might say, “hey, who cares why?”. But it is not. So then it becomes a question of identifying when it will be better.
Again, I had a frustrating email correspondence with Uri and the issues are all clear and do not change the main conclusion of our paper. When there is large heterogeneity, modeling this heterogeneity leads to unbiased estimates of average power, whereas a single component model tends to produce biased estimates.
Brief elaboration on the third point: Cuddy et al. selected incorrect test statistics from problematic studies. Motyl et al. selected lots and lots of incorrect tests. Scraping test-fstatistics is not at all relevant to an assessment of the power of the studies where they came from. These are all unambiguously invalid. Unfortunately, one cannot therefore learn anything about the performance of Z-curve in assessing them.
I really don’t care about Cuddy. What I do care about is that they used p-curve as if it can produce accurate estimates of average power and reported an estimate to readers that suggested they had the right estimate, when p-curve again overestimated average power.
The claims about Motyl are false. I have done my own coding of these studies and despite a few inconsistencies in coding some studies, I get the same results with my coding. Please provide your own coding of these studies and I am sure the results will be the same. Unless you have coded Motyl et al.’s studies, you should not make unbased claims about this dataset or the results that are based on it.
OK, with those in mind, I list below concerns I have with specifics in the paper. These are roughly ordered based on where they occur in the paper:
Really, I would love to stop hear, but I am a bit obsessive compulsive, but readers might have enough information to draw their own conclusions.
* The paper contains are a number of statements of fact that seem too certain. Just one early example, “the most widely used criterion for a successful replication is statistical significance (Killeen, 2005).” That is a common definition and it may be the most common, but that is hardly a certainty (even with a citation). It would be better to simply identify that definition as common and then consider its limitations (while also considering others).
Aside from being the most common, it is also the most reasonable. How else would we compare the results of a study that claimed, the effect is positive, 95%CI d = .03 to .1.26 to the results of a replication study. Would we say, wow replication d = .05, this is consistent with the original study therefore we have a successful replication?
* The following statement seems incorrect (and I think that the authors would be the first to agree with me): “Exact replications of the original study should also produce significant results; at least we should observe more successful than failed replications if the hypothesis is true.” If original studies were all true, but all powered at 25%, then exact (including sample size) replications would be significant 25% of the time. I assume that I am missing the argument, so perhaps I am merely suggesting a simple clarification. (p. 6)
You misinterpret the intention here. We are stating that a good study should be replicable and are implying that a study with 25% power is not a good study. At a minimum we would expect a good study to be more often correct than incorrect which happens when power is over 50%.
* I am not sure that I completely understand the argument about the equivalence of low power and false positives (e.g., “Once we take replicability into account, the distinction between false positives and true positives with low power becomes meaningless, and it is more important to distinguish between studies with good power that are replicable and studies with low power or false positives that are difficult to replicate.”) It seems to me that underpowered original studies may, in the extreme case, be true hypotheses, but they lack meaningful evidence. Alternatively, false positives are definitionally false hypotheses that also, definitionally, lack meaningful evidence. If a replicator were to use a very large sample size, they would certainly care about the difference. Note that I am hardly making a case in support of the underpowered original – I think the authors’ articulations of the importance of statistical power is entirely reasonable – but I think the statement of functional equivalence is a touch cavalier.
Replicability is a property of the original study. If the original study had 6% power it is a bad study, even if a subsequent study with 10 times the sample size is able to show a significant result with much more power.
* I was surprised that there was no discussion of the Simonsohn Small Telescopes perspective in the statistical evaluation of replications. That offers a well-cited and frequently discussed definition of replicability that talks about many of the same issues considered in this introduction. If the authors think that work isn’t worth considering, that is fine, but they might anticipate that other readers would at least wonder why it was not.
The paper is about the replicability of published findings, not about sample size planing for replication studies. Average power predicts what would happen in a study with the same sample sizes, not what would happen if sample sizes were increased. So, the telescope paper is not relevant.
* The consideration of the Reproducibility Project struck me as lacking nuance. It takes the 36% estimate too literally, despite multiple articles and blog posts which have challenged that cut-and-dried interpretation. I think that it would be reasonable to at least give some voice to the Gilbert et al. criticisms which point out that, given the statistical imprecision of the replication studies, a more positive estimate is justifiable. (again, I am guessing that many people – including me – share the general sense of pessimism expressed by the authors, but a one-sided argument will not be persuasive).
Are you nuts? Gilbert may have had one or two points about specific replication studies, but his broader claims about the OSC results are utter nonsense, even if they were published as a commentary in Science. It is a trivial fact that the success rate in a set of studies that is not selected for significance is an estimate of average power. If we didn’t have a file drawer, we could just count the percentage of significant results to know how low power actually is. However, we do have file drawers, and therefore we need a statistical tool like z-curve to estimate average power if that is a desirable goal. If you cannot see that the OSC data are the best possible dataset to evaluate bias-correction methods with heterogeneous data, you seem to lack the most fundamental understanding of statistical power and how it relates to success rates in significance tests.
* The initial description of Z-Curve is generally clear and brief. That is great. On the other hand I think that a reasonable standard should be that readers would need neither to download and run the R-code nor go and read the 2016 paper in order to understand the machinery of the algorithm. Perhaps a few extra sentences to clarify before giving up and sending readers to those other sources.
This is up to the editor. We are happy to move content from the Supplement to the main article or do anything else that can improve clarity and communication. But first we need to be given an opportunity to do so.
* I don’t understand what is happening on pages 11-13. I say that with as much humility as possible, because I am sure that the failing is with me. Nevertheless, I really don’t understand. Is this going to be a telling example? Or is it the structure of the underlying computations? What was the data generating function that made the figure? What is the goal?
* Figure 1: (A few points). The caption mentions “…how Z-curve models…” I am sure that it does, but it doesn’t make sense to me. Perhaps it would be worth clarifying what the inputs are, what the outputs are, what the inferences are, and in general, what the point of the figure is. The authors have spent far more time in creating this figure than anyone else who simply reads it, so I do not doubt that it is a good representation of something, but I am honestly indicating that I do not know what that is. Furthermore, the authors’ say “the dotted black line in Figure 1.” I found it eventually, but it is really hard to see. Perhaps make the other lines a very light gray and the critical line a pure and un-dashed black?
It is a visual representation of the contribution of each component of the model to the total density.
* The authors say that they turn every Z-score of >6 into 6. How consequential is that decision? The explanation that those are all powered at 100% is not sufficient. If there are two results entered into Z-curve one with Z = 7 and one with Z = 12, Z-curve would treat them identically to each other and identically as if they were both Z = 6, right? Is that a strength? (without clarification, it sounds like a weakness). Perhaps it would be worth some sentences and some simulations to clarify the consequences of the arbitrary cutoff. Quite possibly the consequences are zero, but I can’t tell.
Z-curve could also fit components here, but there are few z-scores and if you convert the z-score into power it is pnorm(6, 1.96) = .99997 or 99.997%. So does it matter. No it doesn’t, which is the reason why are doing it. If it would make a difference, we wouldn’t be doing it.
* On p. 13 the authors say, “… the average power estimate was 50% demonstrating large sample accuracy.” That seems like a good solid conclusion inference, but I didn’t understand how they got to it. One possible approach would be to start a bit earlier with clarifying the approach. Something that sounded like, “Our goal was to feed data from a 50% power distribution and then assess the accuracy of Z-curve by seeing whether or not it returned an average estimate of 50%.” From there, perhaps, it might be useful to explain in conversational language how that was conducted.
The main simulations are done later. This is just an example. So we can just delete the claim about large sample accuracy here.
* To reiterate, I simply cannot follow what the authors are doing. I accept that as my fault, but let’s assume that a different reader might share some of my shortcomings. If so, then some extra clarification would be helpful.
Thanks, but if you don’t understand what we are doing, why are you an expert reviewer for our paper. I did ask that Uri is not picked as a reviewer because he ignored all reasonable arguments when I sent him a preprint, but that didn’t mean that some other proponent of p-curve with less statistical background should be the reviewer.
* The authors say that p-curve generates an estimate of 76% for this analysis and that is bad. I believe them. Unfortunately, as I have indicated in a few places, I simply do not understand what the authors did, and so cannot assess the different results.
We used the R-Code for the p-curve app, submitted the data and read the output. And yes, we agree, it is bad that a tool is in the public domain without any warning about bias when there is heterogeneity and the tool can overestimates average power by 25% points. What are you going to do about it?
So clarification would help. Furthermore, the authors then imply that this is due to p-curve’s failure with heterogeneity. That sounds unlikely, given the demonstrations of p-curve’s robustness to heterogeneity (i.e., DataColada), but let’s assume that they are correct.
Uri simulated minimal heterogeneity to save p-curve from embarrassment. So there is nothing surprising here. Uri essentially p-hacked p-curve results to get the results he wanted.
It then becomes absolutely critical for the authors to explain why that particular version is so far off. Based on lengthy exchanges between Uli and Uri, and as referenced in the DataColada post, across large and varied forms of heterogeneity, Z-curve performs worse than p-curve. What is special about this case? Is it one that exists frequently in nature?
Enough already. That p-hacked post is not worth the bytes on the hosting server.
* I understand Figure 2. That is great.
Do we have badges for reviewers who actually understand something in a paper?
* The authors imply that p-curve does worse at estimating high powered studies because of heterogeneity. Is there evidence for that causal claim? It would be great if they could identify the source of the difference.
The evidence is in the fucking paper you were supposed to review and evaluate.
* Uri, in the previous exchanges with Uli (and again, described in the blog post), came to the conclusion that Z-curve did better than p-curve when there were many very extreme (100% power) observations in the presence of other very low powered observations. The effect seemed to be carried by how Z-curve handles those extreme cases. I believe – and truly I am not sure here – that the explanation had to do with the fact that with Z-curve, extreme cases are capped at some upper bound. If that is true then (a) it is REALLY important for that to be described, clarified, and articulated. In addition, (b) it needs to be clearly justified. Is that what we want the algorithm to do? It seems important and potentially persuasive that Z-curve does better with certain distributions, but it clearly does worse with others. Given that, (c) it seems like the best case positioning for Z-curve would be if it could lay out the conditions under which it would perform better (e.g., one in which there are many low powered studies, but the mode was nevertheless >99.99% power), while acknowledging those in which it performs worse (e.g., all of the scenarios laid out in DataColada).
I can read and I read the blog post. I didn’t know these p-hacked simulations would be used against me in the review process.
* Table 1: Rather than presenting these findings in tabular form, I think it would be informative if there were histograms of the studies being entered into Z-curve (as in DataColada). That allows someone to see what is being assessed rather than relying on their intuitive grasp of skewness, for example.
Of course we can add those, but that doesn’t change anything about the facts.
* the Power Posing Meta-Analysis. I think it is interesting to look at how Z-curve evaluates a set of studies. I don’t think that one can evaluate the tool in this way (because we do not know the true power of Power Posing studies), but it is interesting to see. I would make some suggestions though. (a) In a different DataColada post (datacolada.org/66), we looked carefully at the Cuddy, Shultz, & Fosse p-curve and identified that the authors had selected demonstrably incorrect tests from demonstrably problematic studies. I can’t imagine anyone debating either contention (indeed, no one has, though the Z-curve authors might think the studies and tests selected were perfect. That would be interesting to add to this paper.). Those tests were also the most extreme (all >99% power). Without reading this section I would say, “well, no analysis should be run on those test statistics since they are meaningless. On the other hand, since they are extreme in the presence of other very low powered studies, this sounds like exactly the scenario where Z-curve will generate a different estimate from p-curve”. [again, the authors simply cite “heterogeneity” as the explanation and again, that is not informative]. I think that a better comparison might be on the original power-posing p-curve (Simmons & Simonsohn, 2017; datacolada.org/37). Since those test statistics were coded by two authors of the original p-curve, that part is not going to be casually contested. I have no idea what that comparison will look like, but I would be interested.
I don’t care about the silly power-posing research. I can take this out, but it just showed that p-curve is used without understanding its limitations, which have been neglected by the developers of p-curve (not sure how much you were involved).
* The scraping of 995,654 test statistics. I suppose one might wonder “what is the average power of any test reported in psychology between 2010 and 2017?” So long as that is not seen as even vaguely relevant to the power of the studies in which they were reported, then OK. But any implied relevance is completely misleading. The authors link the numbers (68% or 83%) to the results of the Reproducibility Project. That is exactly the type of misleading reporting I am referring to. I would strongly encourage this demonstration to be removed from the paper.
How do we know what the replicability in developmental psychology is? How do we know what the replicability in clinical psychology is? The only information that we have comes from social and experimental cognitive research with simple paradigms. Clearly we cannot generalize to all areas of psychology. Surely an analysis of focal and non-focal tests has some problems that we discuss, but it clearly serves as an upper limit and can be used for termporal and cross-discipline comparisons without taking the absolute numbers too seriously. But this can only be done with a method that is unbiased, not a method that estimates 96% power when power is 75%.
* The Motyl et al p-curve. This is a nice idea, but the data set being evaluated is completely unreasonable to use. In yet another DataColada post (datacolada.org/60), we show that the Motyl et al. researchers selected a number of incorrect tests. Many omnibus tests and many manipulation checks. I honestly think that those authors made a sincere effort but there is no way to use those data in any reasonable fashion. It is certainly no better (and possibly worse) than simply scraping every p-value from each of the included studies. I wish the Motyl et al. study had been very well conducted and that the data were usable. They are not. I recommend that this be removed from the analysis or, time permitting, the Z-curve authors could go through the set of papers and select and document the correct tests themselves.
You are wrong and I haven’t seen you posting a corrected data set. Give me a corrected data set and I bet you $1000 dollar that p-curve will produce a higher estimate than z-curve again.
* Since it is clearly relevant with the above, I will mention that the Z-curve authors do not mention how tests should be selected. Experientially, p-curve users infrequently make mistakes with the statistical procedure, but they frequently make mistakes in the selection of test statistics. I think that if the authors want their tool to be used correctly they would be well served by giving serious consideration to how tests should be selected and then carefully explaining that.
Any statistical method depends on the data you supply. Like when Uri phacked simulations to show that p-curve does well with heterogeneity.
Dear reader (if you made it this far, please let me know in the comments section what you take away from all of this).
The Motyl data are ok, p-curve overestimates, and that is because p-curve doesn’t handle realistic amounts of heterogeneity well.
The Motyl data are ok, p-curve overestimates, but this only happens with the Motyl data.
The Motyl data are ok, p-curve overestimates, but that is because we didn’t use p-curve properly.
The Motyl data are not ok, and our simulations are p-hacked and p-curve does well with heterogeneity.
28 thoughts on “Closed and Biased Peer-Reviews Do not Advance Psychological Science”
PS This needs editing:
Based on the distribution of significant z-scores (z > 1.96), z-curve produced an estimate of However, the z-curve estimate is only 30%
Thank you for your comment. I will fix the sentence.
Without sampling error, results of identical studies would be identical.
Isn’t a possible measure error to be taken into account? Change in temporary mood of population, say world championship win.
Isn’t random measurement error due to uncontrollable situational factors, which is part of the first factor that can produce different results across identical studies?
I dont understand how power equals replicability, since isn’t it also possible that there is no effect (h0 is true)? In other words, if a study that has 50% power rejects h0 with type 1 error, isn’t there a lower than 50% probability that this results would be replicated? This might be a silly question but hopefully you have time to answer me.
Good point. There are two ways to address this.
First, we can think about power of H0 as the power in the limit as effect sizes approach 0
(1 / infinity). As effect sizes become smaller, power decreases to the asymptote of alpha. Practically there is no difference between alpha and power of alpha + 1/infinity.
Another approach is to say that we are not strictly talking about power, but about the probability of a significant result, which is the probability of H0 times alpha + probabilty of H1 * average power. However, because probability of H0 is unknown, we do not know how often H0 is true and we have to settle for estimating the overall average that can be obtained with various percentages of true nulls.
Thank you for you answer. Now it makes sense.
I’m a little confused by this comment: “There are no sign errors in analyses of significant results that cover different research questions.”
I agree with you that sign is just a matter of perspective, but I think the editor was talking about what Gelman refers to as Type S errors, which from what I understand occur when the observed direction of an effect is opposite of the true direction.
For z-curve the question is how replicable published results are.
A simple scenario is that the effect size is 0 and a significant result was reported. In this case, the probability of obtaining a significant result in a replication study is the type-I error probability which is determined by alpha. When we select for alpha = .05, this means the probability is 5%.
If a sign error occurred, it is even less likely that we will replicate a result with the same sign will be replicated and it is know more likely to replicate a result with the opposite sign.
However, this probability is also small because studies with high power do not produce sign errors. If I recall the Gelman article correctly, sign errors are unlikely as soon as studies have 10% power or more.
I have to run actual simulation studies to see how much this issue can contribute to estimation errors, but it has no practical consequences because a large number of sign errors would imply that most studies have very low power and there is no practical difference between estimates of 10% or 20% average power. Any set of studies that produces such low averages (e.g., ego-depletion) is essentially not replicable.
I found this post by Gelman regarding Type S probability: http://andrewgelman.com/2014/11/17/power-06-looks-like-get-used/
Also, you write: “If a study has 80% power it is assumed that the null-hypothesis is false. A study where the null-hypothesis is true has a power of alpha to produce significant results.”
What about the situation where the null is true and the researcher doesn’t care about the direction of the effect (i.e. comes up with a reason to run a one-tailed test posthoc instead of a two-tailed test)?
Actually, one last thing, this might be silly so feel free to ignore it. In my work rounding is the bane of my existence. I don’t know what the inputs are for p-curves and z-curves, but I can imagine that if p-value is the input, and the p-value is extracted from the publications, rounding could be an issue. For example, a value of .005 gets rounded to .01. I have no idea if this could affect the results of p-curves or z-curves, or if the effect might be moderated by other factors such as sample sizes.
1. Simple question first. The input for both methods are test statistics (F values, chi-square values). P-Curve uses the actual non-central distributions of these test-statistics. Z-curve converts all test statistics or exact p-values into absolute z-scores and uses standard normal distributions to model the data.
2. I talked more with Jerry about sign errors after you posted the last question. We use two-sided t-tests or F-tests, and we use power for two-sided z-test. That is, when power is low, we also use the small tail of the distribution at the other end of the distribution. This area is 2.5% for H0 and less than that as power increases. it is practically 0 when you reach 17% power.
So, strictly speaking we cannot make a sign error, but it is possible that a signifiant result in a replication sutdy would be significant with the opposite sign. With H0 = true, 2.5% probability that sign is the same and 2.5% that sign is different. Consistency of sign would require to interpret 2.5% of significant results as error, which would lower the actual power from the nominal 5% to 2.5%.
This is also true for multiple study articles where a set of studies test the same hypothesis. While alpha = 5% assumes significance on either side can be interpreted as a success, only studies that replicate the sign (or are theoretically consistent) can be reported as a success. Thus, alpha is really 2.5% and the risk of a false positive by chance is only 1/40, which means deceptive practices are even more needed to get these 100% successful multiple study articles.
I can’t seem to reply to a reply so I have to post another comment.
Regarding the part where you write: “This is also true for multiple study articles where a set of studies test the same hypothesis.”
I’m not sure if you are referring to the alpha of your method or the alpha of the authors. I would argue that in a multiple study article, for the first study the authors see which direction the wind is blowing, and call that the direction of their effect while using a one-tailed test. As a result, I would say the authors actually had an alpha of 10% for their first study. In each subsequent study they then have to get an effect in a consistent direction, and for these they now have the normal alpha of 5%.
My argument that HARKing is more difficult (not impossible) in a multiple study article and that it may require to show a significant effect in the same direction (same with pre-registration). So, if predicted direction and two-tailed test with alpha = 5%, the actual alpha is 2.5% because only significance in the predicted tail can be sold as a success.
Regarding Leif’s comment: “The authors claim that, relative to Z-curve, p-curve fails under heterogeneity and do not report, comment on, or explain analyses showing exactly the opposite of that assertion.”
I think he is asking you to comment on other people’s comparisons of Z-curve and p-curve.
Thanks again for engaging with this blog post.
What happened here will be presented in detail in a blog post.
The short version is that Uri posted on twitter that it would be good to resolve issues in private before things blow up on social media.
In response to this twitter, I sent Uri a copy of the manuscript that was ready to be submitted.
After a lengthy email exchange that I will publish, Uri never addressed any of the results reported in the manuscript. Instead he came up with his own simulations that showed good behavior of p-curve. The problem is that these simulations are for unrealistic scnenarios (e.g., all studies have n = 20), while my simulations matched data like the Motyl et al. data that were used in a JPSP article to examine the replicability of social psychology.
After Uri was not commenting on the simulation in the paper, I submitted the manuscript falsely assuming that independent reviewers would pay attention to the simulations in the paper or run their own with the r-code that I provided.
Uri posted his self-serving simulations on a blog post which I declined to comment on because I thought a published paper in Advances (LOL) would take care of the blog post.
I also requested that Uri is not a reviewer because he has a conflict of interest and showed no ability to engage with criticism of p-curve.
I did not anticipate that the editor, Dan Simons, would then make another author from the p-curve crew. with the same conflict of interest, a reviewer and that this reviewer would then use the blog post as if it is valid to criticize the manuscript.
Does this sound like open science to you? Maybe Advances need to first advance the way of peer-review before it can advance psychological science. Fortunately, we have a real alternative with open peer review. I will submit all of my work to Meta-Psychology, a journal that is not run by an errorist-organization like APS, that is free for authors and readers, and that has open and transparent peer review. (COI statement: I am co-founder of this journal)
It seems to me that you still actually seem to think/reason that peer-review and publication in an “official” journal are important.
Perhaps the time is right to simply let that stuff go.
Just post it on psyarxiv and let the world (which includes, but is not limited to, the acedemic community) make the most use of it if they want to and/or can.
You can’t control the latter, only the former i reason 🙂
Thanks for your comment. The good news is that blogging and social media has undermined the ability of powerful Errorist organizations to keep critics quiet. I am happy that I can communicate with you here about ways to improve science.
At the same time, it is important that public statements are critically examined and this is hard to achieve on social media. I always ask for comments but rarely receive comments.
I have challenged critics of my rant to give examples where I was unfair and reviewers were right. You can see that nobody took up this challenge. I can say that the reason is that I am 100% right, but why would anybody believe me? So, I think it is necessary and valuable that experts who care about replicability review the manuscript and assess its merits.
“So, I think it is necessary and valuable that experts who care about replicability review the manuscript and assess its merits. ”
Yes, this can be very valuable. I also reason however, that this should not be dependent on 2/3 tradtional peer-reviewers in the traditional journals.
If i were you, and valued feedback but was unable to get some, i would make the judgment of whether i would think it would/could be useful to post it anyway myself.
I reason that if you can’t get others (“peers” or other folks) to provide feedback, then the judgment lies with yourself (thanks to things like psyarxiv which are now available and which i think are very good for open science and improving science).
This is in fact exactly what i have personally done with 2 papers. One of which may be related to what i wrote above about tradtional “peer review” and “official” journals and whether or not (tenured) scientists should still value them and/or be a part of that (deeply flawed) system. For your possible amusement i present the following: https://psyarxiv.com/5vsqw/
Of course. Everything has been published as a preprint. See also pdf link on top of page.
(I couldn’t reply to the following directly but i hope this will be posted just below your reply)
“Of course. Everything has been published as a preprint. See also pdf link on top of page. ”
I saw the pdf link on top of the page, but if i am not mistaken that does not lead to a pre-print posted on Psyarxiv for instance (which would then have possibly additional benefits of receiving a DOI, easier to link to/share, etc.).
We published a preprint on Psyarxiv
“We published a preprint on Psyarxiv
Awesome ! So i reason that now everyone can read it, possibly criticize it, check it, think about it, etc. etc. 57 people may have already downloaded it, and who knows what good will come of that.
The fact that everyone can read it (thanks to the folks behind Psyarxiv/ the Open Science Framework) in my reasoning helps with possible judgment and critique in the sense that I hope this will facilitate it being done according to scientific values and principles etc. (and not based on whether you are friends with the editor and/or reviewer for instance). As long as that’s the case, what more can one expect and hope for concerning science, and why then even bother with tradtional peer-review and journals.
Concerning discussions about/related to traditional peer-review in traditional journals, i always think about the following quote (which i believe exists in a few versions but i like this one by Bruce Lee, because it’s short and it’s Bruce Lee):
“I’m not in this world to live up to your expectations and you’re not in this world to live up to mine.” – Bruce Lee
I made it to the end so I’m going to burden your comment section with this insignificant comment.
Reviewer 2 should not be reviewing this article. His style of review and wording justifies your style of response, I think. His bias is apparent even to the uneducated reader. However the other two reviewers do their best which however is obviously not enough. I think sometimes your wording in the comments aimed at them does the z-curve a disservice.
Some major arguments the reviewers provide are based on blog posts. It’s questionable that they in the same context discredit your blog post citations. Overall the only worthwhile things this review gave you were the typos, ie. it was a waste of everyones time. The reviewers are unjustifiably fixated on the effect sizes, and miss the point of the Z-curve. This is clear in many points, also for example regarding the statements about assumptions. The reviewers’ idea about validation is obviously stuck on one irrelevant schema of how things should be done. It is also alarming that even when they have asked for the R-code they can’t answer their own questions with it.
I appreciate your comments and I am sure that my responses would be different now or a week from now. The post is a reflection of unfiltered (well, that is not true, there was a filter) emotion. I took a risk that some people will now write me off as a crazy narcissist, but I am pretty sure that others have had similar responses to rejection letters that they considered to be unfair. They just don’t post them.
Did I hurt anonymous reviewers? I don’t see how as they chose wisely to remain anonymous.
Did I hurt Reviewer 3 who identified himself? His review made it clear that he was one of the three datacolada authors who are trying to defend their method against my criticism. I understand that outsiders may see the tone as polite and constructive, but that doesn’t change the fact that the arguments are flawed and serve the purpose to shield Reviewer 3’s method from criticism. Of course, that is my opinion, but to evaluate the quality of the review requires understanding the p-curve method and my criticism of it.
I would be most sympathetic with Reviewer 1, who got caught in a cross-fire. It looks like Reviewer 1 was assigned to see whether the manuscript is readable for non-experts and that is clearly not the case. I don’t agree with Reviewer 1 to reject it for this reason (why not give an opportunity to revise it to make it clearer), but again, I was to harsh on Reviewer 1 who seemed to have tried and then got frustrated when he or she failed.
Of course, the main reason for my rant is the editorial decision. I have rewritten whole manuscripts in response to constructive feedback and I was ready to do so for this manuscript, but the editor didn’t give me an opportunity. What was the main reason for this? According to the editor, who is pursuing replication studies, it is not relevant to know a priori whether studies will replicate or not, which has and will lead to more massive replication studies with a predictable outcome that they fail (see ego depletion train wreck). Maybe doing meaningless replication studies is occupational therapy for experimental psychologists who have nothing better to do, but I think it is a terrible waste of resources.
Anyhow, I am ranting again. So, thanks for your constructive and well-balanced comment.