The Red Team Challenge (Part 4): The Wildcard Reviewer

This is a guest blog by Tiago Lubiana, Ph.D. Candidate in Bioinformatics, University of São Paulo.
Read also Part 1, Part 2, and Part 3 of The Red Team Challenge

Two remarkable moments as a researcher are publishing your first first-author article and the first time a journal editor asks you to review a paper.

Well, at least I imagine so. I haven’t experienced either yet. Yet,for some reason, the author of the Red Team Challenge accepted me as a (paid) reviewer for their audacious project.

I believe I am one of the few scientists to receive money for a peer review before doing any unpaid peer-reviews. I’m also perhaps one of the few to review a paper before having any first-author papers. Quite likely, I am the first one to do both at the same time.

I am, nevertheless, a science aficionado. I’ve breathed science for the past 9 years, working in10 different laboratories before joining the Computational Systems Biology Lab at the University of São Paulo, where I am pursuing my PhD. I like this whole thing of understanding more about the world, reading, doing experiments, sharing findings with people. That is my thing (to be fair, that is likely our thing).

I also had my crises with the scientific world. A lot of findings in the literature are contradictory. And many others are simply wrong. And they stay wrong, right? It is incredible, but people usually do not update articles even given a need for corrections. The all-powerful, waxy stamp of peer-reviewed is given to a monolithic text-and-figure-and-table PDF, and this pdf is then frozen forever in the hall of fame. And it costs a crazy amount of money to lock this frozen pdf behind paywalls.

I have always been very thorough in my evaluation of any work. With time, I discovered that, for some reason, people don’t like to have their works criticized (who would imagine, huh?). That can be attenuated by a lot of training in how to communicate. But even then, people frown upon even constructive criticism. If it is a critic about something that is already published, then it is even worse. So I got quite excited when I saw this call for people to have a carte blanche to criticize a piece of work as much as possible.

I got to know the Red Team Challenge via a Whatsapp message sent by Olavo Amaral, who leads the Brazilian Reproducibility Initiative. Well, it looked cool, it paid a fairly decent amount of money, and the application was simple (it did not require a letter of recommendation or anything like this). So I thought: “Why not? I do not know a thing about psychology, but I can maybe spot a few uncorrected multiple comparisons here and there, and I can definitely look at the code.”

I got lucky that the Blue Team (Coles et al.) had a place for random skills (the so-called wildcard category) in their system for selecting reviewers. About a week after applying, I received a message in my mail that stated that I had been chosen as a reviewer. “Great! What do I do now?”

I was obviously a bit scared of making a big blunder or at least just making it way below expectations. But there was a thing that tranquilized me: I was hired. This was not an invitation based on expectations or a pre-existing relationship with the ones hiring me. People were actually paying me, and my tasks for the job were crystal clear.

If I somehow failed to provide a great review, it would not affect my professional life whatsoever (I guess). I had just the responsibility to do a good job that any person has after signing a contract.

I am not a psychologist by training, and so I knew beforehand that the details of the work would be beyond my reach. However, after reading the manuscript, I felt even worse: the manuscript was excellent. Or I mean, at least a lot of care was taken when planning and important experimental details as far as I could tell as an outsider.

It is not uncommon for me to cringe upon a few dangling uncorrected p-values here and there, even when reading something slightly out of my expertise. Or to find some evidence of optional stopping. Or pinpoint some statistical tests from which you cannot really tell what the null hypothesis is and what actually is being tested.

That did not happen. However, everyone involved knew that I was not a psychologist. I was plucked from the class of miscellaneous reviewers. From the start, I knew that I could contribute the most by reviewing the code.

I am a computational biologist, and our peers in the computer sciences usually look down on our code. For example, software engineers called a high profile epidemiological modeling code a “null I would say that lack of computational reproducibility is pervasive throughout science, and not restricted to a discipline or the other.

Luckily, I have always been interested in best practices. I might not always follow them (“do what I say not what I do”), mainly because of environmental constraints. Journals don’t require clean code, for example. And I’ve never heard about “proofreadings” of scripts that come alongside papers.

It was a pleasant surprise to see that the code from the paper was good, better than most of the code I’ve seen in biology-related scripts. It was filled with comments. The required packages were laid down at the beginning of the script. The environment was cleared in the first line so to avoid dangling global variables.

These are all good practices. If journals asked reviewers to check code (which they usually do not), it would come out virtually unscathed.

But I was being paid to review it, so I had to find something. There are some things that can improve one’s code and make it much easier to check and validate. One can avoid commenting too much by using clear variable names, and you do not have to lay down the packages used if the code is containerized (with Docker, for example). A bit of refactoring could be done here and there, also, extracting out functions that were repeatedly used across the code. That was mostly what my review focused on, honestly.

Although these things are relatively minor, they do make a difference. It is a bit like the difference in prose between a non-writer and an experienced writer. The raw content might be the same, but the effectiveness of communication can vary a lot. And reading code can be already challenging, so it is always good to make it easier for the reader (and the reviewer, by extension).

Anyways, I have sent 11 issue reports (below the mean of ~20, but precisely the median of 11 reports/reviewer), and Ruben Arslan, the neutral arbiter, considered one of them to be a major issue. Later, Daniël and Nicholas mentioned that the reviews were helpful, so I am led to believe that somehow I contributed to future improvements in this report. Science wins, I guess.

One interesting aspect of being hired by the authors is that I did not feel compelled to state whether I thought the work was relevant or novel. The work is obviously important for the authors who hired me. The current peer-review system mixes the evaluation of thoroughness and novelty under the same brand. That might be suboptimal in some cases. A good reviewer for statistics, or code, for example, might not feel that they can tell how much a “contribution is significant or only incremental,” as currently required. If that was a requirement for the Red Team Challenge, I would not have been able to be a part of the Red Team.

This mix of functions may be preventing us from getting more efficient reviews. We know that gross mistakes pass peer review. I’d trust a regularly updated preprint, with thorough, open, commissioned peer review, for example. I am sure we can come up with better ways of giving “this-is-good-science” stamps and improve the effectiveness of peer reviews.

To sum up, it felt very good to be in a system with the right incentives. Amidst this whole pandemic thing and chaos everywhere, I ended up being part of something really wonderful. Nicholas, Daniël, and all the others involved in the Red Team challenge are providing prime evidence that an alternate system is viable. Maybe one day, we will have reviewer-for-hire marketplaces and more adequate review incentives. When that day comes, I will be there, be it hiring or being hired.

The Red Team Challenge (Part 3): Is it Feasible in Practice?

By Daniel Lakens & Leo Tiokhin

Also read Part 1 and Part 2 in this series on our Red Team Challenge.

Six weeks ago, we launched the Red Team Challenge: a feasibility study to see whether it could be worthwhile to pay people to find errors in scientific research. In our project, we wanted to see to what extent a “Red Team” – people hired to criticize a scientific study with the goal to improve it – would improve the quality of the resulting scientific work.

Currently, the way that error detection works in science is a bit peculiar. Papers go through the peer-review process and get the peer-reviewed “stamp of approval”. Then, upon publication, some of these same papers receive immediate and widespread criticism. Sometimes this even leads to formal corrections or retractions. And this happens even at some of the most prestigious scientific journals.

So, it seems that our current mechanisms of scientific quality control leave something to be desired. Nicholas Coles, Ruben Arslan, and the authors of this post (Leo Tiokhin and Daniël Lakens) were interested in whether Red Teams might be one way to improve quality control in science.

Ideally, a Red Team joins a research project from the start and criticizes each step of the process. However, doing this would have taken the duration of an entire study. At the time, it also seemed a bit premature — we didn’t know whether anyone would be interested in a Red Team approach, how it would work in practice, and so on. So, instead, Nicholas Coles, Brooke Frohlich, Jeff Larsen, and Lowell Gaertner volunteered one of their manuscripts (a completed study that they were ready to submit for publication). We put out a call on Twitter, Facebook, and the 20% Statistician blog, and 22 people expressed interest. On May 15th, we randomly selected five volunteers based on five areas of expertise: Åse Innes-Ker (affective science), Nicholas James (design/methods), Ingrid Aulike (statistics), Melissa Kline (computational reproducibility), and Tiago Lubiana (wildcard category). The Red Team was then given three weeks to report errors.

Our Red Team project was somewhat similar to traditional peer review, except that we 1) compensated Red Team members’ time with a $200 stipend, 2) explicitly asked the Red Teamers to identify errors in any part of the project (i.e., not just writing), 3) gave the Red Team full access to the materials, data, and code, and 4) provided financial incentives for identifying critical errors (a donation to the GiveWell charity non-profit for each unique “critical error” discovered).

The Red Team submitted 107 error reports. Ruben Arslan–who helped inspire this project with his BugBountyProgram–served as the neutral arbiter. Ruben examined the reports, evaluated the authors’ responses, and ultimately decided whether an issue was “critical” (see this post for Ruben’s reflection on the Red Team Challenge) Of the 107 reports, Ruben concluded that there were 18 unique critical issues (for details, see this project page). Ruben decided that any major issues that potentially invalidated inferences were worth $100, minor issues related to computational reproducibility were worth $20, and minor issues that could be resolved without much work were worth $10. After three weeks, the total final donation was $660. The Red Team detected 5 major errors. These included two previously unknown limitations of a key manipulation, inadequacies in the design and description of the power analysis, an incorrectly reported statistical test in the supplemental materials, and a lack of information about the sample in the manuscript. Minor issues concerned reproducibility of code and clarifications about the procedure.

After receiving this feedback, Nicholas Coles and his co-authors decided to hold off submitting their manuscript (see this post for Nicholas’ personal reflection). They are currently conducting a new study to address some of the issues raised by the Red Team.

We consider this to be a feasibility study of whether a Red Team approach is practical and worthwhile. So, based on this study, we shouldn’t draw any conclusions about a Red Team approach in science except one: it can be done.

That said, our study does provide some food for thought. Many people were eager to join the Red Team. The study’s corresponding author, Nicholas Coles, was graciously willing to acknowledge issues when they were pointed out. And it was obvious that, had these issues been pointed out earlier, the study would have been substantially improved before being carried out. These findings make us optimistic that Red Teams can be useful and feasible to implement.

In an earlier column, the issue was raised that rewarding Red Team members with co-authorship on the subsequent paper would create a conflict of interest — too severe criticism on the paper might make the paper unpublishable. So, instead, we paid each Red Teamer $200 for their service. We wanted to reward people for their time. We did not want to reward them only for finding issues because, before we knew that 19 unique issues would be found, we were naively worried that the Red Team might find few things wrong with the paper. In interviews with Red Team members, it became clear that the charitable donations for each issue were not a strong motivator. Instead, people were just happy to detect issues for decent pay. They didn’t think that they deserved authorship for their work, and several Red Team members didn’t consider authorship on an academic paper to be valuable, given their career goals.

After talking with the Red Team members, we started to think that certain people might enjoy Red Teaming as a job – it is challenging, requires skills, and improves science. This opens up the possibility of a freelance services marketplace (such as Fiverr) for error detection, where Red Team members are hired at an hourly rate and potentially rewarded for finding errors. It should be feasible to hire people to check for errors at each phase of a project, depending on their expertise and reputation as good error-detectors. If researchers do not have money for such a service, they might be able to set up a volunteer network where people “Red Team” each other’s projects. It could also be possible for universities to create Red Teams (e.g., Cornell University has a computational reproducibility service that researchers can hire).

As scientists, we should ask ourselves when, and for which type of studies, we want to invest time and/or money to make sure that published work is as free from errors as possible. As we continue to consider ways to increase the reliability of science, a Red Team approach might be something to further explore.

Red Team Challenge

by Nicholas A. Coles, Leo Tiokhin, Ruben Arslan, Patrick Forscher, Anne Scheel, & Daniël Lakens

All else equal, scientists should trust studies and theories that have been more critically evaluated. The more that a scientific product has been exposed to processes designed to detect flaws, the more that researchers can trust the product (Lakens, 2019; Mayo, 2018). Yet, there are barriers to adopting critical approaches in science. Researchers are susceptible to biases, such as confirmation bias, the “better than average” effect, and groupthink. Researchers may gain a competitive advantage for jobs, funding, and promotions by sacrificing rigor in order to produce larger quantities of research (Heesen, 2018; Higginson & Munafò, 2016) or to win priority races (Tiokhin & Derex, 2019). And even if researchers were transparent enough to allow others to critically examine their materials, code, and ideas, there is little incentive for others–including peer reviewers–to do so. These combined factors may hinder the ability of science to detect errors and self-correct (Vazire, 2019).

Today we announce an initiative that we hope can incentivize critical feedback and error detection in science: the Red Team Challenge. Daniël Lakens and Leo Tiokhin are offering a total of $3,000 for five individuals to provide critical feedback on the materials, code, and ideas in the forthcoming preprint titled “Are facial feedback effects solely driven by demand characteristics? An experimental investigation”. This preprint examines the role of demand characteristics in research on the controversial facial feedback hypothesis: the idea that an individual’s facial expressions can influence their emotions. This is a project that Coles and colleagues will submit for publication in parallel with the Red Team Challenge. We hope that challenge will serve as a useful case study of the role Red Teams might play in science.

We are looking for five individuals to join “The Red Team”. Unlike traditional peer review, this Red Team will receive financial incentives to identify problems. Each Red Team member will receive a $200 stipend to find problems, including (but not limited to) errors in the experimental design, materials, code, analyses, logic, and writing. In addition to these stipends, we will donate $100 to a GoodWell top ranked charity (maximum total donations: $2,000) for every new “critical problem” detected by a Red Team member. Defining a “critical problem” is subjective, but a neutral arbiter–Ruben Arslan–will make these decisions transparently. At the end of the challenge, we will release: (1) the names of the Red Team members (if they wish to be identified), (2) a summary of the Red Team’s feedback, (3) how much each Red Team member raised for charity, and (4) the authors’ responses to the Red Team’s feedback.

If you are interested in joining the Red Team, you have until May 14th to sign up here. At this link, you will be asked for your name, email address, and a brief description of your expertise. If more than five people wish to join the Red Team, we will ad-hoc categorize people based on expertise (e.g., theory, methods, reproducibility) and randomly select individuals from each category. On May 15th, we will notify people whether they have been chosen to join the Red Team.

For us, this is a fun project for several reasons. Some of us are just interested in the feasibility of Red Team challenges in science (Lakens, 2020). Others want feedback about how to make such challenges more scientifically useful and to develop best practices. And some of us (mostly Nick) are curious to see what good and bad might come from throwing their project into the crosshairs of financially-incentivized research skeptics. Regardless of our diverse motivations, we’re united by a common interest: improving science by recognizing and rewarding criticism (Vazire, 2019).

Heesen, R. (2018). Why the reward structure of science makes reproducibility problems inevitable. The Journal of Philosophy, 115(12), 661-674.
Higginson, A. D., & Munafò, M. R. (2016). Current incentives for scientists lead to underpowered studies with erroneous conclusions. PLoS Biology, 14(11), e2000995.
Lakens, D. (2019). The value of preregistration for psychological science: A conceptual analysis. Japanese Psychological Review.

Lakens, D. (2020). Pandemic researchers — recruit your own best critics. Nature, 581, 121.
Mayo, D. G. (2018). Statistical inference as severe testing. Cambridge: Cambridge University Press.
Tiokhin, L., & Derex, M. (2019). Competition for novelty reduces information sampling in a research game-a registered report. Royal Society Open Science, 6(5), 180934.
Vazire, S. (2019). A toast to the error detectors. Nature, 577(9).

What’s a family in family-wise error control?

When you perform multiple comparisons in a study, you need to control your alpha level for multiple comparisons. It is generally recommended to control for the family-wise error rate, but there is some confusion about what a ‘family’ is. As Bretz, Hothorn, & Westfall (2011) write in their excellent book “Multiple Comparisons Using R” on page 15: “The appropriate choice of null hypotheses being of primary interest is a controversial question. That is, it is not always clear which set of hypotheses should constitute the family H1,…,Hm. This topic has often been in dispute and there is no general consensus.” In one of the best papers on controlling for multiple comparisons out there, Bender & Lange (2001) write: “Unfortunately, there is no simple and unique answer to when it is appropriate to control which error rate. Different persons may have different but nevertheless reasonable opinions. In addition to the problem of deciding which error rate should be under control, it has to be defined first which tests of a study belong to one experiment.” The Wikipedia page on family-wise error rate is a mess.

I will be honest: I have never understood this confusion about what a family of tests is when controlling the family-wise error rate. At least not in a Neyman-Pearson approach to hypothesis testing, where the goal is to use data to make decisions about how to act. Neyman (Neyman, 1957) calls his approach inductive behavior. The outcome of an experiment leads one to take different possible actions, which can be either practical (e.g., implement a new procedure, abandon a research line) or scientific (e.g., claim there is or is no effect). From an error-statistical approach (Mayo, 2018) inflated Type 1 error rates mean that it has become very likely that you will be able to claim support for your hypothesis, even when the hypothesis is wrong. This reduces the severity of the test. To prevent this, we need to control our error rate at the level of our claim.
One reason the issue of family-wise error rates might remain vague, is that researchers are often vague about their claims. We do not specify our hypotheses unambiguously, and therefore this issue remains unclear. To be honest, I suspect another reason there is a continuing debate about whether and how to lower the alpha level to control for multiple comparisons in some disciplines is that 1) there are a surprisingly large number of papers written on this topic that argue you do not need to control for multiple comparisons, which are 2) cited a huge number of times giving rise to the feeling that surely they must have a point. Regrettably, the main reason these papers are written is because there are people who don’t think a Neyman-Pearson approach to hypothesis testing is a good idea, and the main reason these papers are cited is because doing so is convenient for researchers who want to publish statistically significant results, as they can justify why they are not lowering their alpha level, making that p = 0.02 in one of three tests really ‘significant’. All papers that argue against the need to control for multiple comparisons when testing hypotheses are wrong.  Yes, their existence and massive citation counts frustrate me. It is fine not to test a hypothesis, but when you do, and you make a claim based on a test, you need to control your error rates. 

But let’s get back to our first problem, which we can solve by making the claims people need to control Type 1 error rates for less vague. Lisa DeBruine and I recently proposed machine readable hypothesis tests to remove any ambiguity in the tests we will perform to examine statistical predictions, and when we will consider a claim corroborated or falsified. In this post, I am going to use our R package ‘scienceverse’ to clarify what constitutes a family of tests when controlling the family-wise error rate.

An example of formalizing family-wise error control

Let’s assume we collect data from 100 participants in a control and treatment condition. We collect 3 dependent variables (dv1, dv2, and dv3). In the population there is no difference between groups on any of these three variables (the true effect size is 0). We will analyze the three dv’s in independent t-tests. This requires specifying our alpha level, and thus deciding whether we need to correct for multiple comparisons. How we control error rates depends on claim we want to make.
We might want to act as if (or claim that) our treatment works if there is a difference between the treatment and control conditions on any of the three variables. In scienceverse terms, this means we consider the prediction corroborated when the p-value of the first t-test is smaller than alpha level, the p-value of the second t-test is smaller than the alpha level, or the p-value of the first t-test is smaller than the alpha level. In the scienceverse code, we specify a criterion for each test (a p-value smaller than the alpha level, p.value < alpha_level) and conclude the hypothesis is corroborated if either of these criteria are met (“p_t_1 | p_t_2 | p_t_3”).  
We could also want to make three different predictions. Instead of one hypothesis (“something will happen”) we have three different hypotheses, and predict there will be an effect on dv1, dv2, and dv3. The criterion for each t-test is the same, but we now have three hypotheses to evaluate (H1, H2, and H3). Each of these claims can be corroborated, or not.
Scienceverse allows you to specify your hypotheses tests unambiguously (for code used in this blog, see the bottom of the post). It also allows you to simulate a dataset, which we can use to examine Type 1 errors by simulating data where no true effects exist. Finally, scienceverse allows you to run the pre-specified analyses on the (simulated) data, and will automatically create a report that summarizes which hypotheses were corroborated (which is useful when checking if the conclusions in a manuscript indeed follow from the preregistered analyses, or not). The output a single simulated dataset for the scenario where we will interpret any effect on the three dv’s as support for the hypothesis looks like this:

Evaluation of Statistical Hypotheses

12 March, 2020

Simulating Null Effects Postregistration


Hypothesis 1: H1

Something will happen

  • p_t_1 is confirmed if analysis ttest_1 yields p.value<0.05

    The result was p.value = 0.452 (FALSE)

  • p_t_2 is confirmed if analysis ttest_2 yields p.value<0.05

    The result was p.value = 0.21 (FALSE)

  • p_t_3 is confirmed if analysis ttest_3 yields p.value<0.05

    The result was p.value = 0.02 (TRUE)

Corroboration ( TRUE )

The hypothesis is corroborated if anything is significant.

 p_t_1 | p_t_2 | p_t_3 

Falsification ( FALSE )

The hypothesis is falsified if nothing is significant.

 !p_t_1 & !p_t_2 & !p_t_3 

All criteria were met for corroboration.

We see the hypothesis that ‘something will happen’ is corroborated, because there was a significant difference on dv3 – even though this was a Type 1 error, since we simulated data with a true effect size of 0 – and any difference was taken as support for the prediction. With a 5% alpha level, we will observe 1-(1-0.05)^3 = 14.26% Type 1 errors in the long run. This Type 1 error inflation can be prevented by lowering the alpha level, for example by a Bonferroni correction (0.05/3), after which the expected Type 1 error rate is 4.92% (see Bretz et al., 2011, for more advanced techniques to control error rates). When we examine the report for the second scenario, where each dv tests a unique hypothesis, we get the following output from scienceverse:

Evaluation of Statistical Hypotheses

12 March, 2020

Simulating Null Effects Postregistration


Hypothesis 1: H1

dv1 will show an effect

  • p_t_1 is confirmed if analysis ttest_1 yields p.value<0.05

    The result was p.value = 0.452 (FALSE)

Corroboration ( FALSE )

The hypothesis is corroborated if dv1 is significant.


Falsification ( TRUE )

The hypothesis is falsified if dv1 is not significant.


All criteria were met for falsification.

Hypothesis 2: H2

dv2 will show an effect

  • p_t_2 is confirmed if analysis ttest_2 yields p.value<0.05

    The result was p.value = 0.21 (FALSE)

Corroboration ( FALSE )

The hypothesis is corroborated if dv2 is significant.


Falsification ( TRUE )

The hypothesis is falsified if dv2 is not significant.


All criteria were met for falsification.

Hypothesis 3: H3

dv3 will show an effect

  • p_t_3 is confirmed if analysis ttest_3 yields p.value<0.05

    The result was p.value = 0.02 (TRUE)

Corroboration ( TRUE )

The hypothesis is corroborated if dv3 is significant.


Falsification ( FALSE )

The hypothesis is falsified if dv3 is not significant.


All criteria were met for corroboration.

We now see that two hypotheses were falsified (yes, yes, I know you should not use p > 0.05 to falsify a prediction in real life, and this part of the example is formally wrong so I don’t also have to explain equivalence testing to readers not familiar with it – if that is you, read this, and know scienceverse will allow you to specify equivalence test as the criterion to falsify a prediction, see the example here). The third hypothesis is corroborated, even though, as above, this is a Type 1 error.

It might seem that the second approach, specifying each dv as it’s own hypothesis, is the way to go if you do not want to lower the alpha level to control for multiple comparisons. But take a look at the report of the study you have performed. You have made 3 predictions, of which 1 was corroborated. That is not an impressive success rate. Sure, mixed results happen, and you should interpret results not just based on the p-value (but on the strength of the experimental design, assumptions about power, your prior, the strength of the theory, etc.) but if these predictions were derived from the same theory, this set of results is not particularly impressive. Since researchers can never selectively report only those results that ‘work’ because this would be a violation of the code of research integrity, we should always be able to see the meager track record of predictions.If you don’t feel ready to make a specific predictions (and run the risk of sullying your track record) either do unplanned exploratory tests, and do not make claims based on their results, or preregister all possible tests you can think of, and massively lower your alpha level to control error rates (for example, genome-wide association studies sometimes use an alpha level of 5 x 10–8 to control the Type 1 erorr rate).

Hopefully, specifying our hypotheses (and what would corroborate them) transparently by using scienceverse makes it clear what happens in the long run in both scenarios. In the long run, both the first scenario, if we would use an alpha level of 0.05/3 instead of 0.05, and the second scenario, with an alpha level of 0.05 for each individual hypothesis, will lead to the same end result: Not more than 5% of our claims will be wrong, if the null hypothesis is true. In the first scenario, we are making one claim in an experiment, and in the second we make three. In the second scenario we will end up with more false claims in an absolute sense, but the relative number of false claims is the same in both scenarios. And that’s exactly the goal of family-wise error control.
Bender, R., & Lange, S. (2001). Adjusting for multiple testing—When and how? Journal of Clinical Epidemiology, 54(4), 343–349.
Bretz, F., Hothorn, T., & Westfall, P. H. (2011). Multiple comparisons using R. CRC Press.
Mayo, D. G. (2018). Statistical inference as severe testing: How to get beyond the statistics wars. Cambridge University Press.
Neyman, J. (1957). “Inductive Behavior” as a Basic Concept of Philosophy of Science. Revue de l’Institut International de Statistique / Review of the International Statistical Institute, 25(1/3), 7.

Thanks to Lisa DeBruine for feedback on an earlier draft of this blog post.

Review of "Do Effect Sizes in Psychology Laboratory Experiments Mean Anything in Reality?"

Researchers spend a lot of time reviewing papers. These reviews are rarely made public. Sometimes reviews might be useful for readers of an article. Here, I’m sharing my review of “Do Effect Sizes in Psychology Laboratory Experiments Mean Anything in Reality? by Roy Baumeister. I reviewed this (blinded) manuscript in December 2019 for a journal where it was rejected January 8 based on 2 reviews. Below you can read the review as I submitted it. I am sharing this review because the paper was accepted at another journal. 

In this opinion piece the authors try to argue for the lack of theoretical meaning of effect sizes in psychology. The opinion piece makes a point I think most reasonable people already agreed upon (social psychology makes largely ordinal predictions). The question is how educational and well argued their position is that this means effect sizes are theoretically not that important. On that aspect, I found the paper relatively weak. Too many statements are overly simplistic and the text is far behind on the state of the art (it reads as if it was written 20 years ago). I think a slightly brushed up version might make a relatively trivial but generally educational point for anyone not up to speed on this topic. If the author put in a bit more effort to have a discussion that incorporates the state of the art, this could be a more nuanced piece that has a bit stronger analysis of the issues at play, and a bit more vision about where to go. I think the latter would be worth reading for a general audience at this journal.

Main points.

1) What is the real reason our theories do not predict effect sizes?

The authors argue how most theories in social psychology are verbal theories. I would say most verbal theories in social psych are actually not theories (Fiedler, 2004) but closer to tautologies. That being said, I think the anecdotal examples the authors use throughout their paper (obedience effects, bystander effect, cognitive dissonance) are all especially weak, and the paper would be improved if all these examples are removed. Although the authors are correct in stating we hardly care about the specific effect size in those studies, I am not interested in anecdotes of studies where we know we do not care about effect sizes. This is a weak (as in, not severe) test of the argument the authors are making, with confirmation bias dripping from every sentence. If you want to make a point about effect sizes not mattering, you can easily find situations where they do not theoretically matter. But this is trivial and boring. What would be more interesting is an analysis of why we do not care about effect sizes that generalizes beyond the anecdotal examples. The authors are close, but do not provide such a general argument yet. One reason I think the authors would like to mention is that there is a measurement crisis in psych – people use a hodgepodge of often completely unvalidated measures. It becomes a lot more interesting to quantify effect sizes if we all use the same measurement. This would also remove the concern about standardized vs unstandardized effect sizes. But more generally, I think the authors should make an argument more from basic principles, than based on anecdotes, if they want to be convincing.

2) When is something an ordinal prediction?

Now, if we use the same measures, are there cases where we predict effect sizes? The authors argue we never predict an exact effect size. True, but again, uninteresting. We can predict a range of effect sizes. The authors cite Meehl, but they should really incorporate Meehl’s point from his 1990 paper. Predicting a range of effect sizes is already quite something, and the authors do not give this a fair discussion. It matters a lot if I predict an effect in the range of 0.2 to 0.8, even though this is very wide, then if I say I predict any effect larger than zero. Again, a description of the state of the art is missing in the paper. This question has been discussed in many literatures the authors do not mention. The issue is the same as the discussion about whether we should use a uniform prior in Bayesian stats, or a slightly more informative prior, because we predict effects in some range. My own work specifying the smallest effect size of interest also provides quite a challenge to the arguments of the current authors. See especially the example of Burriss and colleages in our 2018 paper (Lakens, Scheel, & Isager, 2018). They predicted an effect should be noticeable with the naked eye, and it is an example where a theory very clearly makes a range prediction, falsifying the authors arguments in the current paper. That these cases exist, means the authors are completely wrong in their central thesis. It also means they need to rephrase their main argument – when do we have range predictions, and when are we predicting *any* effect that is not zero. And why? I think many theories in psychology would argue that effects should be larger than some other effect size. This can be sufficient to make a valid range prediction. Similarly, if psychologist would just think about effect sizes that are too large, we would not have papers in PNAS edited by Nobel prize winners that think the effect of judges on parole decisions over time is a psychological mechanism, when the effect size is too large to be plausible (Glöckner, 2016). So effects should often be larger or smaller than some value, and this does not align with the current argument by the authors.  
I would argue the fact that psych theories predict range effects means psych theories make effect size predictions that are relevant enough to quantify. We do a similar thing when we compare 2 conditions, for example when we predict an effect is larger in condition X than Y. In essence, this means we say: We predict the effect size of X to be in a range that is larger than the effect size of Y. Now, this is again a range prediction. We do not just say both X and Y have effects that differ from zero. It is still an ordinal prediction, so fits with the basic point of the authors about how we predict, but it no longer fits with their argument that we simply test for significance. Ordinal predictions can be more complex than the authors currently describe. To make a solid contribution they will need to address what ordinal predictions are in practice. With the space that is available after the anecdotes are removed, they can add a real analysis of how we test hypotheses in general, where range predictions fit with ordinal predictions, and if we would use the same measures and have some widely used paradigms, we could, if we wanted to, create theories that make quantifiable range predictions. I agree with the authors it can be perfectly valid to choose a unique operationalization of a test, and that this allows you to increase or decrease the effect size depending on the operationalization. This is true. But we can make theories that predict things beyond just any effect if we fix our paradigms and measures – and authors should discuss if this might be desirable to give their own argument a bit more oomph and credibility. If the authors want to argue that standard measures in psychology are undesirable or impossible, that might be interesting, but I doubt it will work. And thus, I expect author will need to give more credit to the power of ordinal predictions. In essence, my point here is that if you think we can not make a range prediction on a standardized measure, you also think there can be no prediction that condition X yields a larger effect than condition y, and yet we make these predictions all the time. Again, in a Stroop effect with 10 trials effect sizes differ than is we have 10000 trials – but given a standardized measure, we can predict relative differences.

3) Standardized vs unstandardized effect sizes

I might be a bit too rigid here, but when scientists make claims, I like them to be accompanied by evidence. The authors write “Finally, it is commonly believed that in the case of arbitrary units, a standardized effect size is more meaningful and informative than its equivalent in raw score units.” There is no citation and this to me sounds 100% incorrect. I am sure they might be able to dig out one misguided paper making this claim. But this is not commonly believed, and the literature abundantly shows researchers argue the opposite – the most salient example is (Baguley, 2009) but any stats book would suffice. The lack of a citation to Baguley is just one of the examples where the authors seem not to be up to speed of the state of the art, and where their message is not nuanced enough, while the discussion in the literature surpassed many of their simple claims more than a decade ago. I think the authors should improve their discussion of standardized and unstandardized effect sizes. Standardized effect sizes are useful of measurement tools differ, and if you have little understanding of what you are measuring. Although I think this is true in general in social psychology (and the measurement crisis is real), I think the authors are not making the point that *given* that social psychology is such a mess when it comes to how researchers in the field measure things, we can not make theoretically quantifiable predictions. I would agree with this. I think they try to argue that even if social psychology was not such a mess, we could still not make quantifiable predictions. I disagree. Issues related to the standardized and unstandardized effect sizes are a red herring. They do not matter anything. If we understood our measures and standardized them, we would have accurate estimates of the sd’s for what we are interested in, and this whole section can just be deleted. The authors should be clear if they think we will never standardize our measures and there is no value in them or if it is just difficult in practice right now. Regardless, they issue with standardized effects is mute, since their first sentence that standardized effect sizes are more meaningful is just wrong (for a discussion, Lakens, 2013).

Minor points

When discussing Festinger and Carlsmith, it makes sense to point out how low quality and riddled with mistakes the study was:
The authors use the first studies of several classic research lines as an example that psychology predicts directional effects at best, and that these studies cared about demonstrating an effect. Are the authors sure their idea of scientific progress is that we for ever limit ourselves to demonstrating effects? This is criticized in many research fields, and the idea of developing computational models in in some domains deserves to be mentioned. Even a simple stupid model can make range predictions that can be tested theoretically. A broader discussion of psychologists who have a bit more ambition for social psychology than the current authors, and who believe that some progress towards even a rough computational model would allow us to predict not just ranges, but also the shapes of effects (e.g., linear vs exponential effects) would be warranted, I think. I think it is fine if the authors have the opinion that social psychology will not move along by more quantification. But I find the final paragraph a bit vague and uninspiring in what the vision is. No one argues against practical applications or conceptual replications. The authors rightly note it is easier (although I think not as much easier as the authors think) to use effects in cost-benefit analyses in applied research. But what is the vision? Demonstration proofs and an existentialistic leap of faith that we can apply things? That has not worked well. Applied psychological researchers have rightly criticized theoretically focused social psychologists for providing basically completely useless existence proofs that often do not translate to any application, and are too limited to be of any value. I do not know what the solution is here, but I would be curious to hear if the authors have a slightly more ambitious vision. If not, that is fine, but if they have one, I think it would boost the impact of the paper.
Daniel Lakens
Baguley, T. (2009). Standardized or simple effect size: What should be reported? British Journal of Psychology, 100(3), 603–617.
Fiedler, K. (2004). Tools, toys, truisms, and theories: Some thoughts on the creative cycle of theory formation. Personality and Social Psychology Review, 8(2), 123–131.
Glöckner, A. (2016). The irrational hungry judge effect revisited: Simulations reveal that the magnitude of the effect is overestimated. Judgment and Decision Making, 11(6), 601–610.
Lakens, D. (2013). Calculating and reporting effect sizes to facilitate cumulative science: A practical primer for t-tests and ANOVAs. Frontiers in Psychology, 4.
Lakens, D., Scheel, A. M., & Isager, P. M. (2018). Equivalence Testing for Psychological Research: A Tutorial. Advances in Methods and Practices in Psychological Science, 1(2), 259–269.

Review of "The Generalizability Crisis" by Tal Yarkoni

A response to this blog by Tal Yarkoni is here.
In a recent preprint titled “The Generalizability Crisis“, Tal Yarkoni examines whether the current practice of how psychologists generalize from studies to theories is problematic. He writes: “The question taken up in this paper is whether or not the tendency to generalize psychology findings far beyond the circumstances in which they were originally established is defensible. The case I lay out in the next few sections is that it is not, and that unsupported generalization lies at the root of many of the methodological and sociological challenges currently affecting psychological science.” We had a long twitter discussion about the paper, and then read it in our reading group. In this review, I try to make my thoughts about the paper clear in one place, which might be useful if we want to continue to discuss whether there is a generalizability crisis, or not.

First, I agree with Yarkoni that almost all the proposals he makes in the section “Where to go from here?” are good suggestions. I don’t think they follow logically from his points about generalizability, as I detail below, but they are nevertheless solid suggestions a researcher should consider. Second, I agree that there are research lines in psychology where modelling more things as random factors will be productive, and a forceful manifesto (even if it is slightly less practical than similar earlier papers) might be a wake up call for people who had ignored this issue until now.

Beyond these two points of agreement, I found the main thesis in his article largely unconvincing. I don’t think there is a generalizability crisis, but the article is a nice illustration of why philosophers like Popper abandoned the idea of an inductive science. When Yarkoni concludes that “A direct implication of the arguments laid out above is that a huge proportion of the quantitative inferences drawn in the published psychology literature are so inductively weak as to be at best questionable and at worst utterly insensible.” I am primarily surprised he believes induction is a defensible philosophy of science. There is a very brief discussion of views by Popper, Meehl, and Mayo on page 19, but their work on testing theories is proposed as a probable not feasible solution – which is peculiar, because these authors would probably disagree with most of the points made by Yarkoni, and I would expect at least somewhere in the paper a discussion comparing induction against the deductive approach (especially since the deductive approach is arguably the dominant approach in psychology, and therefore none of the generalizability issues raised by Yarkoni are a big concern). Because I believe the article starts from a faulty position (scientists are not concerned with induction, but use deductive approaches) and because Yarkoni provides no empirical support for any of his claims that generalizability has led to huge problems (such as incredibly high Type 1 error rates), I remain unconvinced there is anything remotely close to the generalizability crisis he so evocatively argues for. The topic addressed by Yarkoni is very broad. It probably needs a book length treatment to do it justice. My review is already way too long, and I did not get into the finer details of the argument. But I hope this review helps to point out the parts of the manuscript where I feel important arguments lack a solid foundation, and where issues that deserve to be discussed are ignored.

Point 1: “Fast” and “slow” approaches need some grounding in philosophy of science.

Early in the introduction, Yarkoni says there is a “fast” and “slow” approach of drawing general conclusions from specific observations. Whenever people use words that don’t exactly describe what they mean, putting them in quotation marks is generally not a good idea. The “fast” and “slow” approaches he describes are not, I believe upon closer examination, two approaches “of drawing general conclusions from specific observations”.

The difference is actually between induction (the “slow” approach of generalizing from single observations to general observations) and deduction, as proposed by for example Popper. As Popper writes “According to the view that will be put forward here, the method of critically testing theories, and selecting them according to the results of tests, always proceeds on the following lines. From a new idea, put up tentatively, and not yet justified in any way—an anticipation, a hypothesis, a theoretical system, or what you will—conclusions are drawn by means of logical deduction.”

Yarkoni incorrectly suggests that “upon observing that a particular set of subjects rated a particular set of vignettes as more morally objectionable when primed with a particular set of cleanliness-related words than with a particular set of neutral words, one might draw the extremely broad conclusion that ‘cleanliness reduces the severity of moral judgments’”. This reverses the scientific process as proposed by Popper, which is (as several people have argued, see below) the dominant approach to knowledge generation in psychology. The authors are not concluding that “cleanliness reduces the severity of moral judgments” from their data. This would be induction. Instead, they are positing that “cleanliness reduces the severity of moral judgments”, they collected data and performed and empirical test, and found their hypothesis was corroborated. In other words, the hypothesis came first. It is not derived from the data – the hypothesis is what led them to collect the data.

Yarkoni deviates from what is arguably the common approach in psychological science, and suggests induction might actually work: “Eventually, if the e?ect is shown to hold when systematically varying a large number of other experimental factors, one may even earn the right to summarize the results of a few hundred studies by stating that “cleanliness reduces the severity of moral judgments””. This approach to science flies right in the face of Popper (1959/2002, p. 10), who says: “I never assume that we can argue from the truth of singular statements to the truth of theories. I never assume that by force of ‘verified’ conclusions, theories can be established as ‘true’, or even as merely ‘probable’.” Similarly, Lakatos (1978, p. 2) writes: “One can today easily demonstrate that there can be no valid derivation of a law of nature from any finite number of facts; but we still keep reading about scientific theories being proved from facts. Why this stubborn resistance to elementary logic?” I am personally on the side of Popper and Lakatos, but regardless of my preferences, Yarkoni needs to provide some argument his inductive approach to science has any possibility of being a success, preferably by embedding his views in some philosophy of science. I would also greatly welcome learning why Popper and Lakatos are wrong. Such an argument, which would overthrow the dominant model of knowledge generation in psychology, could be impactful, although a-priori I doubt it will be very successful.

Point 2: Titles are not evidence for psychologist’s tendency to generalize too quickly.

This is a minor point, but I think a good illustration of the weakness of some of the main arguments that are made in the paper. On the second page, Yarkoni argues that “the vast majority of psychological scientists have long operated under a regime of (extremely) fast generalization”. I don’t know about the vast majority of scientists, but Yarkoni himself is definitely using fast generalization. He looked through a single journal, and found 3 titles that made general statements (e.g., “Inspiration Encourages Belief in God”). When I downloaded and read this article, I noticed the discussion contains a ‘constraint on generalizability’ in the discussion, following (Simons et al., 2017). The authors wrote: “We identify two possible constraints on generality. First, we tested our ideas only in American and Korean samples. Second, we found that inspiring events that encourage feelings of personal insignificance may undermine these effects.”. Is Yarkoni not happy with these two sentence clearly limiting the generalizability in the discussion?

For me, this observation raised serious concerns about the statement Yarkoni makes that, simply from the titles of scientific articles, we can make a statement about whether authors make ‘fast’ or ‘slow’ generalizations. One reason is that Yarkoni examined titles from a scientific article that adheres to the publication manual of the APA. In the section on titles, the APA states: “A title should summarize the main idea of the manuscript simply and, if possible, with style. It should be a concise statement of the main topic and should identify the variables or theoretical issues under investigation and the relationship between them. An example of a good title is “Effect of Transformed Letters on Reading Speed.””. To me, it seems the authors are simply following the APA publication manual. I do not think their choice for a title provides us with any insight whatsoever about the tendency of authors to have a preference for ‘fast’ generalization. Again, this might be a minor point, but I found this an illustrative example of the strength of arguments in other places (see the next point for the most important example). Yarkoni needs to make a case that scientists are overgeneralizing, for there to be a generalizability crisis – but he does so unconvincingly. I sincerely doubt researchers expect their findings to generalize to all possible situations mentioned in the title, I doubt scientists believe titles are the place to accurately summarize limits of generalizability, and I doubt Yarkoni has made a strong point that psychologists overgeneralize based on this section. More empirical work would be needed to build a convincing case (e.g., code how researchers actually generalize their findings in a random selection of 250 articles, taking into account Gricean communication norms (especially the cooperative principle) in scientific articles).

Point 3: Theories and tests are not perfectly aligned in deductive approaches.

After explaining that psychologists use statistics to test predictions based on experiments that are operationalizations of verbal theories, Yarkoni notes: “From a generalizability standpoint, then, the key question is how closely the verbal and quantitative expressions of one’s hypothesis align with each other.”

Yarkoni writes: “When a researcher verbally expresses a particular hypothesis, she is implicitly defining a set of admissible observations containing all of the hypothetical situations in which some measurement could be taken that would inform that hypothesis. If the researcher subsequently asserts that a particular statistical procedure provides a suitable test of the verbal hypothesis, she is making the tacit but critical assumption that the universe of admissible observations implicitly defined by the chosen statistical procedure (in concert with the experimental design, measurement model, etc.) is well aligned with the one implicitly defined by the qualitative hypothesis. Should a discrepancy between the two be discovered, the researcher will then face a choice between (a) working to resolve the discrepancy in some way (i.e., by modifying either the verbal statement of the hypothesis or the quantitative procedure(s) meant to provide an operational parallel); or (b) giving up on the link between the two and accepting that the statistical procedure does not inform the verbal hypothesis in a meaningful way.

I highlighted what I think is the critical point is in a bold font. To generalize from a single observation to a general theory through induction, the sample and the test should represent the general theory. This is why Yarkoni is arguing that there has to be a direct correspondence between the theoretical model, and the statistical test. This is true in induction.

If I want to generalize beyond my direct observations, which are rarely sampled randomly from all possible factors that might impact my estimate, I need to account for uncertainty in the things I have not observed. As Yarkoni clearly explains, one does this by adding random factors to a model. He writes (p. 7) “Each additional random factor one adds to a model licenses generalization over a corresponding population of potential measurements, expanding the scope of inference beyond only those measurements that were actually obtained. However, adding random factors to one’s model also typically increases the uncertainty with which the fixed e?ects of interest are estimated”. You don’t need to read Popper to see the problem here – if you want to generalize to all possible random factors, there are so many of them, you will never be able to overcome the uncertainty and learn anything. This is why inductive approaches to science have largely been abandoned. As Yarkoni accurately summarizes based on an large multi-lab study on verbal overshadowing by Alogna: “given very conservative background assumptions, the massive Alogna et al. study—an initiative that drew on the efforts of dozens of researchers around the world—does not tell us much about the general phenomenon of verbal overshadowing. Under more realistic assumptions, it tells us essentially nothing.” This is also why Yarkoni’s first practical recommendation on how to move forward is to not solve the problem, but to do something else: “One perfectly reasonable course of action when faced with the difficulty of extracting meaningful, widely generalizable conclusions from e?ects that are inherently complex and highly variable is to opt out of the enterprise entirely.”

This is exactly the reason Popper (among others) rejected induction, and proposed a deductive approach. Why isn’t the alignment between theories and tests raised by Yarkoni a problem for the deductive approach proposed by Popper, Meehl, and Mayo? The reason is that the theory is tentatively posited as true, but in no way believed to be a complete representation of reality. This is an important difference. Yarkoni relies on an inductive approach, and thus the test needs to be aligned with the theory, and the theory defines “a set of admissible observations containing all of the hypothetical situations in which some measurement could be taken that would inform that hypothesis.” For deductive approaches, this is not true.

For philosophers of science like Popper and Lakatos, a theory is not a complete description of reality. Lakatos writes about theories: “Each of them, at any stage of its development, has unsolved problems and undigested anomalies. All theories, in this sense, are born refuted and die refuted.” Lakatos gives the example that Newton’s Principia could not even explain the motion of the moon when it was published. The main point here: All theories are wrong. The fact that all theories (or models) are wrong should not be surprising. Box’s quote “All models are wrong, some are useful” is perhaps best known, but I prefer Box (1976) on parsimony: “Since all models are wrong the scientist cannot obtain a “correct” one by excessive elaboration. On the contrary following William Ockham (1285-1349) he should seek an economical description of natural phenomena. Just as the ability to devise simple but evocative models is the signature of the great scientist so overelaboration and overparameterization is often the mark of mediocrity (Ockham’s knife).” He follows this up by stating “Since all models are wrong the scientist must be alert to what is importantly wrong. It is inappropriate to be concerned about mice when there are tigers abroad.”

In a deductive approach, the goal of a theoretical model is to make useful predictions. I doubt anyone believes that any of the models they are currently working on is complete. Some researchers might follow an instrumentalist philosophy of science, and don’t expect their theories to be anything more than useful tools. Lakatos’s (1978) main contribution to philosophy of science was to develop a way we deal with our incorrect theories, admitting that all needed adjustment, but some adjustments lead to progressive research lines, and others to degenerative research lines.

In a deductive model, it is perfectly fine to posit a theory that eating ice-cream makes people happy, without assuming this holds for all flavors, across all cultures, at all temperatures, and is irrespective of the amount of ice-cream eaten previously, and many other factors. After all, it is just a tentatively model that we hope is simple enough to be useful, and that we expect to become more complex as we move forward. As we increase our understanding of food preferences, we might be able to modify our theory, so that it is still simple, but also allows us to predict the fact that eggnog and bacon flavoured ice-cream do not increase happiness (on average). The most important thing is that our theory is tentative, and posited to allow us to make good predictions. As long as the theory is useful, and we have no alternatives to replace it with, the theory will continue to be used – without any expectation that is will generalize to all possible situations. As Box (1976) writes: “Matters of fact can lead to a tentative theory. Deductions from this tentative theory may be found to be discrepant with certain known or specially acquired facts. These discrepancies can then induce a modified, or in some cases a different, theory.” A discussion of this large gap between Yarkoni and deductive approaches proposed by Popper and Meehl, where Yarkoni thinks theories and tests need to align, and deductive approaches see theories as tentative and wrong, should be included, I think. 

Point 4: The dismissal of risky predictions is far from convincing (and generalizability is typically a means to risky predictions, not a goal in itself).

If we read Popper (but also on the statistical side the work of Neyman) we see induction as a possible goal in science is clearly rejected. Yarkoni mentions deductive approaches briefly in his section on adopting better standards, in the sub-section on making riskier predictions. I intuitively expected this section to be crucial – after all, it finally turns to those scholars who would vehemently disagree with most of Yarkoni’s arguments in the preceding sections – but I found this part rather disappointing. Strangely enough, Yarkoni simply proposes predictions as a possible solution – but since the deductive approach goes directly against the inductive approach proposed by Yarkoni, it seems very weird to just mention risky predictions as one possible solution, when it is actually a completely opposite approach that rejects most of what Yarkoni argues for. Yarkoni does not seem to believe that the deductive mode proposed by Popper, Meehl, and Mayo, a hypothesis testing approach that is arguably the dominant approach in most of psychology (Cortina & Dunlap, 1997; Dienes, 2008; Hacking, 1965), has a lot of potential. The reason he doubts severe tests of predictions will be useful is that “in most domains of psychology, there are pervasive and typically very plausible competing explanations for almost every finding” (Yarkoni, p. 19). This could be resolved if risky predictions were possible, which Yarkoni doubts.

Yarkoni’s criticism on the possibility of severe tests is regrettably weak. Yarkoni says that “Unfortunately, in most domains of psychology, there are pervasive and typically very plausible competing explanations for almost every finding.” From his references (Cohen, Lykken, Meehl) we can see he refers to the crud factor, or the idea that the null hypothesis is always false. As we recently pointed out in a review paper on crud (Orben & Lakens, 2019), Meehl and Lykken disagreed about the definition of the crud factor, the evidence of crud in some datasets can not be generalized to all studies in pychology, and “The lack of conceptual debate and empirical research about the crud factor has been noted by critics who disagree with how some scientists treat the crud factor as an “axiom that needs no testing” (Mulaik, Raju, & Harshman, 1997).”. Altogether, I am very unconvinced by this cursory reference to crud makes a convincing point that “there are pervasive and typically very plausible competing explanations for almost every finding”. Risky predictions seem possible, to me, and demonstrating the generalizability of findings is actually one way to perform a severe test.

When Yarkoni discusses risky predictions, he sticks to risky quantitative predictions. As explained in Lakens (2020), “Making very narrow range predictions is a way to make it statistically likely to falsify your prediction if it is wrong. But the severity of a test is determined by all characteristics of a study that increases the capability of a prediction to be wrong, if it is wrong. For example, by predicting you will only observe a statistically significant difference from zero in a hypothesis test if a very specific set of experimental conditions is met that all follow from a single theory, it is possible to make theoretically risky predictions.” I think the reason most psychologists perform studies that demonstrate the generalizability of their findings has nothing to do with their desire to inductively build a theory from all these single observations. They show the findings generalize, because it increases the severity of their tests. In other words, according to this deductive approach, generalizability is not a goal in itself, but a it follows from the goal to perform severe tests. It is unclear to me why Yarkoni does not think that approaches such as triangulation (Munafò & Smith, 2018) are severe tests. I think these approaches are the driving force between many of the more successful theories in social psychology (e.g., social identity theory), and it works fine.

Generalization as a means to severely test a prediction is common, and one of the goals of direct replications (generalizing to new samples) and conceptual replications (generalizing to different procedures). Yarkoni might disagree with me that generalization serves severity, not vice versa. But then what is missing from the paper is a solid argument why people would want to generalize to begin with, assuming at least a decent number of them do not believe in induction. The inherent conflict between the deductive approaches and induction is also not explained in a satisfactory manner.

Point 5: Why care about statistical inferences, if these do not relate to sweeping verbal conclusions?

If we ignore all points previous points, we can still read Yarkoni’s paper as a call to introduce more random factors in our experiments. This nicely complements recent calls to vary all factors you do not thing should change the conclusions you draw (Baribault et al., 2018), and classic papers on random effects (Barr et al., 2013; Clark, 1969; Cornfield & Tukey, 1956).

Yarkoni generalizes from the fact that most scientists model subjects as a random factor, and then asks why scientists generalize to all sorts of other factors that were not in their models. He asks “Why not simply model all experimental factors, including subjects, as fixed e?ects”. It might be worth noting in the paper that sometimes researchers model subjects as fixed effects. For example, Fujisaki and Nishida (2009) write: “Participants were the two authors and five paid volunteers” and nowhere in their analyses do they assume there is any meaningful or important variation across individuals. In many perception studies, an eye is an eye, and an ear is an ear – whether from the author, or a random participant dragged into the lab from the corridor.

In other research areas, we do model individuals as a random factor. Yarkoni says we model stimuli as a random factor because: “The reason we model subjects as random e?ects is not that such a practice is objectively better, but rather, that this specification more closely aligns the meaning of the quantitative inference with the meaning of the qualitative hypothesis we’re interested in evaluating”. I disagree. I think we model certain factor as random effects because we have a high prior these factors influence the effect, and leaving them out of the model would reduce the strength of our prediction. Leaving them out reduces the probability a test will show we are wrong, if we are wrong. It impacts the severity of the test. Whether or not we need to model factors (e.g., temperature, the experimenter, or day of the week) as random factors because not doing so reduces the severity of a test is a subjective judgments. Research fields need to decide for themselves. It is very well possible more random factors are generally needed, but I don’t know how many, and doubt it will ever be as severe are the ‘generalizability crisis’ suggests. If it is as severe as Yarkoni suggests, some empirical demonstrations of this would be nice. Clark (1973) showed his language-as-fixed-effect fallacy using real data. Barr et al (2013) similarly made their point based on real data. I currently do not find the theoretical point very strong, but real data might convince me otherwise.

The issues about including random factors is discussed in a more complete, and importantly, applicable, manner in Barr et al (2013). Yarkoni remains vague on which random factors should be included and which not, and just recommends ‘more expansive’ models. I have no idea when this is done satisfactory. This is a problem with extreme arguments like the one Yarkoni puts forward. It is fine in theory to argue your test should align with whatever you want to generalize to, but in practice, it is impossible. And in the end, statistics is just a reasonably limited toolset that tries to steer people somewhat in the right direction. The discussion in Barr et al (2013), which includes trade-offs between converging models (which Yarkoni too easily dismisses as solved by modern computational power – it is not solved) and including all possible factors, and interactions between all possible factors, is a bit more pragmatic. Similarly, Cornfield & Tukey (1956) more pragmatically list options ranging from ignoring factors altogether, to randomizing them, or including them as a factor, and note “Each of these attitudes is appropriate in its place. In every experiment there are many variables which could enter, and one of the great skills of the experimenter lies in leaving out only inessential ones.” Just as pragmatically, Clark (1973) writes: “The wide-spread capitulation to the language-as-fixed-effect fallacy, though alarming, has probably not been disastrous. In the older established areas, most experienced investigators have acquired a good feel for what will replicate on a new language sample and what will not. They then design their experiments accordingly.” As always, it is easy to argue for extremes in theory, but this is generally uninteresting for an applied researcher. It would be great if Yarkoni could provide something a bit more pragmatic about what to do in practice than his current recommendation about fitting “more expansive models” – and provides some indication where to stop, or at least suggestions what an empirical research program would look like that tells us where to stop, and why. In some ways, Yarkoni’s point generalizes the argument that most findings in psychology do not generalize to non-WEIRD populations (Henrich et al., 2010), and it has the same weakness. WEIRD is a nice acronym, but it is just a completely random collection of 5 factors that might limit generalizability. The WEIRD acronym functions more as a nice reminder that boundary conditions exist, but it does not allow us to predict when they exist, or when they matter enough to be included in our theories. Currently, there is a gap between the factors that in theory could matter, and the factors that we should in practice incorporate. Maybe it is my pragmatic nature, but without such a discussion, I think the paper offers relatively little progress compared to previous discussions about generalizability (of which there are plenty).


A large part of Yarkoni’s argument is based on the fact that theories and tests should be closely aligned, while in a deductive approach based on severe tests of predictions, models are seen as simple, tentative, and wrong, and this is not considered a problem. Yarkoni does not convincingly argue researchers want to generalize extremely broadly (although I agree papers would benefit from including Constraints on Generalizability statements a proposed by Simons and colleagues (2017), but mainly because this improves falsifiability, not because it improves induction), and even if there is the tendency to overclaim in articles, I do not think this leads to an inferential crisis. Previous authors have made many of the same points, but in a more pragmatic manner (e.g., Barr et al., 2013m Clark, 1974,). Yarkoni fails to provide any insights into where the balance between generalizing to everything, and generalizing to factors that matter, should lie, nor does he provide an evaluation of how far off this balance research areas are. It is easy to argue any specific approach to science will not work in theory – but it is much more difficult to convincingly argue it does not work in practice. Until Yarkoni does the latter convincingly, I don’t think the generalizability crisis as he sketches it is something that will keep me up at night.


Baribault, B., Donkin, C., Little, D. R., Trueblood, J. S., Oravecz, Z., Ravenzwaaij, D. van, White, C. N., Boeck, P. D., & Vandekerckhove, J. (2018). Metastudies for robust tests of theory. Proceedings of the National Academy of Sciences, 115(11), 2607–2612.

Barr, D. J., Levy, R., Scheepers, C., & Tily, H. J. (2013). Random effects structure for confirmatory hypothesis testing: Keep it maximal. Journal of Memory and Language, 68(3).

Box, G. E. (1976). Science and statistics. Journal of the American Statistical Association, 71(356), 791–799.

Clark, H. H. (1969). Linguistic processes in deductive reasoning. Psychological Review, 76(4), 387–404.

Cornfield, J., & Tukey, J. W. (1956). Average Values of Mean Squares in Factorials. The Annals of Mathematical Statistics, 27(4), 907–949.

Cortina, J. M., & Dunlap, W. P. (1997). On the logic and purpose of significance testing. Psychological Methods, 2(2), 161.

Dienes, Z. (2008). Understanding psychology as a science: An introduction to scientific and statistical inference. Palgrave Macmillan.

Fujisaki, W., & Nishida, S. (2009). Audio–tactile superiority over visuo–tactile and audio–visual combinations in the temporal resolution of synchrony perception. Experimental Brain Research, 198(2), 245–259.

Hacking, I. (1965). Logic of Statistical Inference. Cambridge University Press.

Henrich, J., Heine, S. J., & Norenzayan, A. (2010). Most people are not WEIRD. Nature, 466(7302), 29–29.

Lakens, D. (2020). The Value of Preregistration for Psychological Science: A Conceptual Analysis. Japanese Psychological Review.

Munafò, M. R., & Smith, G. D. (2018). Robust research needs many lines of evidence. Nature, 553(7689), 399–401.

Orben, A., & Lakens, D. (2019). Crud (Re)defined.

Simons, D. J., Shoda, Y., & Lindsay, D. S. (2017). Constraints on Generality (COG): A Proposed Addition to All Empirical Papers. Perspectives on Psychological Science, 12(6), 1123–1128.

Observed Type 1 Error Rates (Why Statistical Models are Not Reality)

“In the long run we are all dead.” – John Maynard Keynes
When we perform hypothesis tests in a Neyman-Pearson framework we want to make decisions while controlling the rate at which we make errors. We do this in part by setting an alpha level that guarantees we will not say there is an effect when there is no effect more than ?% of the time, in the long run.
I like my statistics applied. And in practice I don’t do an infinite number of studies. As Keynes astutely observed, I will be dead before then. So when I control the error rate for my studies, what is a realistic Type 1 error rate I will observe in the ‘somewhat longer run’?
Let’s assume you publish a paper that contains only a single p-value. Let’s also assume the true effect size is 0, so the null hypothesis is true. Your test will return a p-value smaller than your alpha level (and this would be a Type 1 error) or not. With a single study, you don’t have the granularity to talk about a 5% error rate.

In experimental psychology 30 seems to be a reasonable average for the number of p-values that are reported in a single paper ( Let’s assume you perform 30 tests in a single paper and every time the null is true (even though this is often unlikely in a real paper). In the long run, with an alpha level of 0.05 we can expect that 30 * 0.05 = 1.5 p-values will be significant. But in real sets of 30 p-values there is no half of a p-value, so you will either observe 0, 1, 2, 3, 4, 5, or even more Type 1 errors, which equals 0%, 3.33%, 6.66%, 10%, 13.33%, 16.66%, or even more. We can plot the frequency of Type 1 error rates for 1 million sets of 30 tests.

Each of these error rates occurs with a certain frequency. 21.5% of the time, you will not make any Type 1 errors. 12.7% of the time, you will make 3 Type 1 errors in 30 tests. The average over thousands of papers reporting 30 tests will be a Type 1 error rate of 5%, but no single set of studies is average.

Now maybe a single paper with 30 tests is not ‘long runnerish’ enough. What we really want to control the Type 1 error rate of is the literature, past, present, and future. Except, we will never read the literature. So let’s assume we are interested in a meta-analysis worth of 200 studies that examine a topic where the true effect size is 0 for each test. We can plot the frequency of Type 1 error rates for 1 million sets of 200 tests.

Now things start to look a bit more like what you would expect. The Type 1 error rate you will observe in your set of 200 tests is close to 5%. However, it is almost exactly as likely that the observed Type 1 error rate is 4.5%. 90% of the distribution of observed alpha levels will lie between 0.025 and 0.075. So, even in ‘somewhat longrunnish’ 200 tests, the observed Type 1 error rate will rarely be exactly 5%, and it might be more useful to think about it as being between 2.5 and 7.5%.

Statistical models are not reality.

A 5% error rate exists only in the abstract world of infinite repetitions, and you will not live long enough to perform an infinite number of studies. In practice, if you (or a group of researchers examining a specific question) do real research, the error rates are somewhere in the range of 5%. Everything has variation in samples drawn from a larger population – error rates are no exception.
When we quantify things, there is the tendency to get lost in digits. But in practice, the levels of random noise we can reasonable expect quickly overwhelms everything at least 3 digits after the decimal. I know we can compute the alpha level after a Pocock correction for two looks at the data in sequential analyses as 0.0294. But this is not the level of granularity that we should have in mind when we think of the error rate we will observe in real lines of research. When we control our error rates, we do so with the goal to end up somewhere reasonably low, after a decent number of hypotheses have been tested. Whether we end up observing 2.5% Type 1 errors or 7.5% errors: Potato, patato.
This does not mean we should stop quantifying numbers precisely when they can be quantified precisely, but we should realize what we get from the statistical procedures we use. We don’t get a 5% Type 1 error rate in any real set of studies we will actually perform. Statistical inferences guide us roughly to where we would ideally like to end up. By all means calculate exact numbers where you can. Strictly adhere to hard thresholds to prevent you from fooling yourself too often. But maybe in 2020 we can learn to appreciate statistical inferences are always a bit messy. Do the best you reasonably can, but don’t expect perfection. In 2020, and in statistics.

For a related paper on alpha levels that in practical situations can not be 5%, see by Casper Albers. 

Do You Really Want to Test a Hypothesis?

I’ve uploaded one of my favorite lectures in the my new MOOC “Improving Your Statistical Questions” to YouTube. It asks the question whether you really want to test a hypothesis. A hypothesis is a very specific tool to answer a very specific question. I like hypothesis tests, because in experimental psychology it is common to perform lines of research where you can design a bunch of studies that test simple predictions about the presence or absence of differences on some measure. I think they have a role to play in science. I also think hypothesis testing is widely overused. As we are starting to do hypothesis tests better (e.g., by preregisteringour predictions and controlling our error rates in more severe tests) I predict many people will start to feel a bit squeamish as they become aware that doing hypothesis tests as they were originally designed to be used isn’t really want they want in their research. One of the often overlooked gains in teaching people how to do something well, is that they finally realize that they actually don’t want to do it.
The lecture “Do You Really Want to Test a Hypothesis” aims to explain which question a hypothesis tests asks, and discusses when a hypothesis tests answers a question you are interested in. It is very easy to say what not to do, or to point out what is wrong with statistical tools. Statistical tools are very limited, even under ideal circumstances. It’s more difficult to say what you can do. If you follow my work, you know that this latter question is what I spend my time on. Instead of telling you optional stopping can’t be done because it is p-hacking, I explain how you can do it correctly through sequential analysis. Instead of telling you it is wrong to conclude the absence of an effect from p > 0.05, I explain how to use equivalence testing­­. Instead of telling you p-values are the devil, I explain how they answer a question you might be interested in when used well. Instead of saying preregistration is redundant, I explain from which philosophy of science preregistration has value. And instead of saying we should abandon hypothesis tests, I try to explain in this video how to use them wisely. This is all part of my ongoing #JustifyEverything educational tour. I think it is a reasonable expectation that researchers should be able to answer at least a simple ‘why’ question if you ask why they use a specific tool, or use a tool in a specific manner.
This might help to move beyond the simplistic discussion I often see about these topics. If you ask me if I prefer frequentist of Bayesian statistics, or confirmatory or exploratory research, I am most likely to respond ? (see Wikipedia). It is tempting to think about these topics in a polarized either-or mindset – but then you would miss asking the real questions. When would any approach give you meaningful insights? Just as not every hypothesis test is an answer to a meaningful question, so will not every exploratory study provide interesting insights. The most important question to ask yourself when you plan a study is ‘when will the tools you use lead to interesting insights’? In the second week of my MOOC I discuss when effects in hypothesis tests could be deemed meaningful, but the same question applies to exploratory or descriptive research. Not all exploration is interesting, and we don’t want to simply describe every property of the world. Again, it is easy to dismiss any approach to knowledge generation, but it is so much more interesting to think about which tools willlead to interesting insights. And above all, realize that in most research lines, researchers will have a diverse set of questions that they want to answer given practical limitations, and they will need to rely on a diverse set of tools, limitations and all.
In this lecture I try to explain what the three limitations are of hypothesis tests, and the very specific question they try to answer. If you like to think about how to improve your statistical questions, you might be interested in enrolling in my free MOOC Improving Your Statistical Questions”.

The Value of Preregistration for Psychological Science: A Conceptual Analysis

This blog is an excerpt of an invited journal article for a special issue of Japanese Psychological Review, that I am currently one week overdue with (but that I hope to complete soon). I hope this paper will raise the bar in the ongoing discussion about the value of preregistration in psychological science. If you have any feedback on what I wrote here, I would be very grateful to hear it, as it would allow me to improve the paper I am working on. If we want to fruitfully discuss preregistration, researchers need to provide a clear conceptual definition of preregistration, anchored in their philosophy of science.
For as long as data has been used to support scientific claims, people have tried to selectively present data in line with what they wish to be true. In his treatise ‘On the Decline of Science in England: And on Some of its Cases’ Babbage (1830) discusses what he calls cooking: “One of its numerous processes is to make multitudes of observations, and out of these to select those only which agree or very nearly agree. If a hundred observations are made, the cook must be very unlucky if he can not pick out fifteen or twenty that will do up for serving.” In the past researchers have proposed solutions to prevent bias in the literature. With the rise of the internet it has become feasible to create online registries that ask researchers to specify their research design and the planned analyses. Scientific communities have started to make use of this opportunity (for a historical overview, see Wiseman, Watt, & Kornbrot, 2019).
Preregistration in psychology has been a good example of ‘learning by doing’. Best practices are continuously updated as we learn from practical challenges and early meta-scientific investigations into how preregistrations are performed. At the same time, discussions have emerged about what the goal of preregistration is, whether preregistration is desirable, and what preregistration should look like across different research areas. Every practice comes with costs and benefits, and it is useful to evaluate whether and when preregistration is worth it. Finally, it is important to evaluate how preregistration relates to different philosophies of science, and when it facilitates or distracts from goals scientists might have. The discussion about benefits and costs of preregistration has not been productive up to now because there is a general lack of a conceptual analysis of what preregistration entails and aims to accomplish, which leads to disagreements that are easily resolved when a conceptual definition would be available. Any conceptual definition about a tool that scientists use, such as preregistration, must examine the goals it achieves, and thus requires a clearly specified view on philosophy of science, which provides an analysis of different goals scientists might have. Discussing preregistration without discussing philosophy of science is a waste of time.

What is Preregistration For?

Preregistration has the goal to transparently prevent bias due to selectively reporting analyses. Since bias in estimates only occurs in relation to a true population parameter, preregistration as discussed here is limited to scientific questions that involve estimates of population values from samples. Researchers can have many different goals when collecting data, perhaps most notably theory development, as opposed to tests of statistical predictions derived from theories. When testing predictions, researchers might want a specific analysis to yield a null effect, for example to show that including a possible confound in an analysis does not change their main results. More often perhaps, they want an analysis to yield a statistically significant result, for example so that they can argue the results support their prediction, based on a p-value below 0.05. Both examples are sources of bias in the estimate of a population effect size. In this paper I will assume researchers use frequentist statistics, but all arguments can be generalized to Bayesian statistics (Gelman & Shalizi, 2013). When effect size estimates are biased, for example due to the desire to obtain a statistically significant result, hypothesis tests performed on these estimates have inflated Type 1 error rates, and when bias emerges due to the desire to obtain a non-significant test result, hypothesis tests have reduced statistical power. In line with the general tendency to weigh Type 1 error rates (the probability of obtaining a statistically significant result when there is no true effect) as more serious than Type 2 error rates (the probability of obtaining a non-significant result when there is a true effect), publications that discuss preregistration have been more concerned with inflated Type 1 error rates than with low power. However, one can easily think of situations where the latter is a bigger concern.
If the only goal of a researcher is to prevent bias it suffices to make a mental note of the planned analyses, or to verbally agree upon the planned analysis with collaborators, assuming we will perfectly remember our plans when analyzing the data. The reason to write down an analysis plan is not to prevent bias, but to transparently prevent bias. By including transparency in the definition of preregistration it becomes clear that the main goal of preregistration is to convince others that the reported analysis tested a clearly specified prediction. Not all approaches to knowledge generation value prediction, and it is important to evaluate if your philosophy of science values prediction to be able to decide if preregistration is a useful tool in your research. Mayo (2018) presents an overview of different arguments for the role prediction plays in science and arrives at a severity requirement: We can build on claims that passed tests that were highly capable of demonstrating the claim was false, but supported the prediction nevertheless. This requires that researchers who read about claims are able to evaluate the severity of a test. Preregistration facilitates this.
Although falsifying theories is a complex issue, falsifying statistical predictions is straightforward. Researchers can specify when they will interpret data as support for their claim based on the result of a statistical test, and when not. An example is a directional (or one-sided) t-test testing whether an observed mean is larger than zero. Observing a value statistically smaller or equal to zero would falsify this statistical prediction (as long as statistical assumptions of the test hold, and with some error rate in frequentist approaches to statistics). In practice, only range predictions can be statistically falsified. Because resources and measurement accuracy are not infinitely large, there is always a value close enough to zero that is statistically impossible to distinguish from zero. Therefore, researchers will need to specify at least some possible outcomes that would not be considered support for their prediction that statistical tests can pick up on. How such bounds are determined is a massively understudied problem in psychology, but it is essential to have falsifiable predictions.
Where bounds of a range prediction enable statistical falsification, the specification of these bounds is not enough to evaluate how highly capable a test was to demonstrate a claim was wrong. Meehl (1990) argues that we are increasingly impressed by a prediction, the more ways a prediction could have been wrong.  He writes (1990, p. 128): “The working scientist is often more impressed when a theory predicts something within, or close to, a narrow interval than when it predicts something correctly within a wide one.” Imagine making a prediction about where a dart will land if I throw it at a dartboard. You will be more impressed with my darts skills if I predict I will hit the bullseye, and I hit the bullseye, than when I predict to hit the dartboard, and I hit the dartboard. Making very narrow range predictions is a way to make it statistically likely to falsify your prediction, if it is wrong. It is also possible to make theoretically risky predictions, for example by predicting you will only observe a statistically significant difference from zero in a hypothesis test if a very specific set of experimental conditions is met that all follow from a single theory. Regardless of how researchers increase the capability of a test to be wrong, the approach to scientific progress described here places more faith in claims based on predictions that have a higher capability of being falsified, but where data nevertheless supports the prediction. Anyone is free to choose a different philosophy of science, and create a coherent analysis of the goals of preregistration in that framework, but as far as I am aware, Mayo’s severity argument currently provides one of the few philosophies of science that allows for a coherent conceptual analysis of the value of preregistration.
Researchers admit to research practices that make their predictions, or the empirical support for their prediction, look more impressive than it is. One example of such a practice is optional stopping, where researchers collect a number of datapoints, perform statistical analyses, and continue the data collection if the result is not statistically significant. In theory, a researcher who is willing to continue collecting data indefinitely will always find a statistically significant result. By repeatedly looking at the data, the Type 1 error rate can inflate to 100%. Even though in practice the inflation will be smaller, optional stopping strongly increases the probability that a researcher can interpret their result as support for their prediction. In the extreme case, where a researcher is 100% certain that they will observe a statistically significant result when they perform their statistical test, their prediction will never be falsified. Providing support for a claim by relying on optional stopping should not increase our faith in the claim by much, or even at all. As Mayo (2018, p. 222) writes: “The good scientist deliberately arranges inquiries so as to capitalize on pushback, on effects that will not go away, on strategies to get errors to ramify quickly and force us to pay attention to them. The ability to register how hunting, optional stopping, and cherry picking alter their error-probing capacities is a crucial part of a method’s objectivity.” If researchers were to transparently register their data collection strategy, readers could evaluate the capability of the test to falsify their prediction, conclude this capability is very small, and be relatively unimpressed by the study. If the stopping rule keeps the probability of finding a non-significant result when the prediction is incorrect high, and the data nevertheless support the prediction, we can choose to act as if the claim is correct because it has been severely tested. Preregistration thus functions as a tool to allow other researchers te transparently evaluate the severity with which a claim has been tested.
The severity of a test can also be compromised by selecting a hypothesis based on the observed results. In this practice, known as Hypothesizing After the Results are Known (HARKing, Kerr, 1998) researchers look at their data, and then select a prediction. This reversal of the typical hypothesis testing procedure makes the test incapable of demonstrating the claim was false. Mayo (2018) refers to this as ‘bad evidence, no test’. If we choose a prediction from among the options that yield a significant result, the claims we make base on these ‘predictions’ will never be wrong. In philosophies of science that value predictions, such claims do not increase our confidence that the claim is true, because it has not yet been tested. By preregistering our predictions, we transparently communicate to readers that our predictions predated looking at data, and therefore that the data we present as support of our prediction could have falsified our hypothesis. We have not made our test look more severe by narrowing the range of our predictions after looking at the data (like the Texas sharpshooter who draws the circles of the bullseye after shooting at the wall of the barn). A reader can transparently evaluate how severely our claim was tested.
As a final example of the value of preregistration to transparently allow readers to evaluate the capability of our prediction to be falsified, think about the scenario described by Babbage at the beginning of this article, where a researchers makes multitudes of observations, and selects out of all these tests only those that support their prediction. The larger the number of observations to choose from, the higher the probability that one of the possible tests could be presented as support for the hypothesis. Therefore, from a perspective on scientific knowledge generation where severe tests are valued, choosing to selectively report tests from among many tests that were performed strongly reduces the capability of a test to demonstrate the claim was false. This can be prevented by correcting for multiple testing by lowering the alpha level depending on the number of tests.
The fact that preregistration is about specifying ways in which your claim could be false is not generally appreciated. Preregistrations should carefully specify not just the analysis researchers plan to perform, but also when they would infer from the analyses that their prediction was wrong. As the preceding section explains, successful predictions impress us more when the data that was collected was capable of falsifying the prediction. Therefore, a preregistration document should give us all the required information that allows us to evaluate the severity of the test. Specifying exactly which test will be performed on the data is important, but not enough. Researchers should also specify when they will conclude the prediction was not supported. Beyond specifying the analysis plan in detail, the severity of a test can be increased by narrowing the range of values that are predicted (without increasing the Type 1 and Type 2 error rate), or making the theoretical prediction more specific by specifying detailed circumstances under which the effect will be observed, and when it will not be observed.

When is preregistration valuable?

If one agrees with the conceptual analysis above, it follows that preregistration adds value for people who choose to increase their faith in claims that are supported by severe tests and predictive successes. Whether this seems reasonable depends on your philosophy of science. Preregistration itself does not make a study better or worse compared to a non-preregistered study. Sometimes, being able to transparently evaluate a study (and its capability to demonstrate claims were false) will reveal a study was completely uninformative. Other times we might be able to evaluate the capability of a study to demonstrate a claim was false even if the study is not transparently preregistered. Examples are studies where there is no room for bias, because the analyses are perfectly constrained by theory, or because it is not possible to analyze the data in any other way than was reported. Although the severity of a test is in principle unrelated to whether it is pre-registered or not, in practice there will be a positive correlation that is caused by the studies where the ability to evaluate how capable these studies were to demonstrate a claim was false is improved by transparently preregistering, such as studies with multiple dependent variables to choose from, which do not use standardized measurement scale so that the dependent variable can be calculated in different ways, or where additional data is easily collected, to name a few.
We can apply our conceptual analysis of preregistration to hypothetical real-life situations to gain a better insight into when preregistration is a valuable tool, and when not. For example, imagine a researcher who preregisters an experiment where the main analysis tests a linear relationship between two variables. This test yields a non-significant result, thereby failing to support the prediction. In an exploratory analysis the authors find that fitting a polynomial model yields a significant test result with a low p-value. A reviewer of their manuscript has studied the same relationship, albeit in a slightly different context and with another measure, and has unpublished data from multiple studies that also yielded polynomial relationships. The reviewer also has a tentative idea about the underlying mechanism that causes not a linear, but a polynomial, relationship. The original authors will be of the opinion that the claim of a polynomial relationship has passed a less severe test than their original prediction of a linear prediction would have passed (had it been supported). However, the reviewer would never have preregistered a linear relationship to begin with, and therefore does not evaluate the switch to a polynomial test in the exploratory result section as something that reduces the severity of the test. Given that the experiment was well-designed, the test for a polynomial relationship will be judged as having greater severity by the reviewer than by the authors. In this hypothetical example the reviewer has additional data that would have changed the hypothesis they would have preregistered in the original study. It is also possible that the difference in evaluation of the exploratory test for a polynomial relationship is based purely on a subjective prior belief, or on the basis of knowledge about an existing well-supported theory that would predict a polynomial, but not a linear, relationship.
Now imagine that our reviewer asks for the raw data to test whether their assumed underlying mechanism is supported. They receive the dataset, and looking through the data and the preregistration, the reviewer realizes that the original authors didn’t adhere to their preregistered analysis plan. They violated their stopping rule, analyzing the data in batches of four and stopping earlier than planned. They did not carefully specify how to compute their dependent variable in the preregistration, and although the reviewer has no experience with the measure that has been used, the dataset contains eight ways in which the dependent variable was calculated. Only one of the eight ways in which the dependent variable yields a significant effect for the polynomial relationship. Faced with this additional information, the reviewer believes it is much more likely that the analysis testing the claim was the result of selective reporting, and now is of the opinion the polynomial relationship was not severely tested.
Both of these evaluations of how severely a hypothesis was tested were perfectly reasonable, given the information reviewer had available. It reveals how sometimes switching from a preregistered analysis to an exploratory analysis does not impact the evaluation of the severity of the test by a reviewer, while in other cases a selectively reported result does reduce the perceived severity with which a claim has been tested. Preregistration makes more information available to readers that can be used to evaluate the severity of a test, but readers might not always evaluate the information in a preregistration in the same way. Whether a design or analytic choice increases or decreases the capability of a claim to be falsified depends on statistical theory, as well as on prior beliefs about the theory that is tested. Some practices are known to reduce the severity of tests, such as optional stopping and selective reporting analyses that yield desired results, and therefore it is easier to evaluate how statistical practices impact the severity with which a claim is tested. If a preregistration is followed through exactly as planned then the tests that are performed have desired error rates in the long run, as long as the test assumptions are met. Note that because long run error rates are based on assumptions about the data generating process, which are never known, true error rates are unknown, and thus preregistration makes it relatively more likely that tests have desired long run error rates. The severity of a tests also depends on assumptions about the underlying theory, and how the theoretical hypothesis is translated into a statistical hypothesis. There will rarely be unanimous agreement on whether a specific operationalization is a better or worse test of a hypothesis, and thus researchers will differ in their evaluation of how severely specific design choices tests a claim. This once more highlights how preregistration does not automatically increase the severity of a test. When it prevents practices that are known to reduce the severity of tests, such as optional stopping, preregistration leads to a relative increase in the severity of a test compared a non-preregistered study. But when there is no objective evaluation of the severity of a test, as is often the case when we try to judge how severe a test was based on theoretical grounds, preregistration merely enables a transparent evaluation of the capability of a claim to be falsified.

Improving Your Statistical Questions

Three years after launching my first massive open online course (MOOC) ‘Improving Your Statistical Inferences’ on Coursera, today I am happy to announce a second completely free online course called ‘Improving Your Statistical Questions’. My first course is a collection of lessons about statistics and methods that we commonly use, but that I wish I had known how to use better when I was taking my first steps into empirical research. My new course is a collection of lessons about statistics and methods that we do not yet commonly use, but that I wish we start using to improve the questions we ask. Where the first course tries to get people up to speed about commonly accepted best practices, my new course tries to educate researchers about better practices. Most of the modules consist of topics in which there has been more recent developments, or at least increasing awareness, over the last 5 years.

About a year ago, I wrote on this blog: If I ever make a follow up to my current MOOC, I will call it ‘Improving Your Statistical Questions’. The more I learn about how people use statistics, the more I believe the main problem is not how people interpret the numbers they get from statistical tests. The real issue is which statistical questions researchers ask from their data. If you approach a statistician to get help with the data analysis, most of their time will be spend asking you ‘but what is your question?’. I hope this course helps to take a step back, reflect on this question, and get some practical advice on how to answer it.
There are 5 modules, with 15 videos, and 13 assignments that provide hands on explanations of how to use the insights from the lectures in your own research. The first week discusses different questions you might want to ask. Only one of these is a hypothesis test, and I examine in detail if you really want to test a hypothesis, or are simply going through the motions of the statistical ritual. I also discuss why NHST is often not a very risky prediction, and why range predictions are a more exciting question to ask (if you can). Module 2 focuses on falsification in practice and theory, including a lecture and some assignments on how to determine the smallest effect size of interest in the studies you perform. I also share my favorite colloquium question for whenever you dozed of and wake up at the end only to find no one else is asking a question, when you can always raise you hand to ask ‘so, what would falsify your hypothesis?’ Module 3 discusses the importance of justifying error rates, a more detailed discussion on power analysis (following up on the ‘sample size justification’ lecture in MOOC1), and a lecture on the many uses of learning how to simulate data. Module 4 moves beyond single studies, and asks what you can expect from lines of research, how to perform a meta-analysis, and why the scientific literature does not look like reality (and how you can detect, and prevent contributing to, a biased literature). I was tempted to add this to MOOC1, but I am happy I didn’t, as there has been a lot of exciting work on bias detection that is now part of the lecture. The last module has three different topics I think are important: computational reproducibility, philosophy of science (this video would also have been a good first video lecture, but I don’t want to scare people away!) and maybe my favorite lecture in the MOOC on scientific integrity in practice. All are accompanied by assignments, and the assignments is where the real learning happens.
If after this course some people feel more comfortable to abandon hypothesis testing and just describe their data, make their predictions a bit more falsifiable, design more informative studies, publish sets of studies that look a bit more like reality, and make their work more computationally reproducible, I’ll be very happy.
The content of this MOOC is based on over 40 workshops and talks I gave in the last 3 years since my previous MOOC came out, testing this material on live crowds. It comes with some of the pressure a recording artist might feel for a second record when their first was somewhat successful. As my first MOOC hits 30k enrolled learners (many of who attend very few of the content, but still with thousands of people taking in a lot of the material) I hope it comes close and lives up to expectations.
I’m very grateful to Chelsea Parlett Pelleriti who checked all assignments for statistical errors or incorrect statements, and provided feedback that made every exercise in this MOOC better. If you need a statistics editor, you can find her at: Special thanks to Tim de Jonge who populated the Coursera environment as a student assistant, and Sascha Prudon for recording and editing the videos. Thanks to Uri Simonsohn for feedback on Assignment 2.1, Lars Penke for suggesting the SESOI example in lecture 2.2, Lisa DeBruine for co-developing Assignment 2.4, Joe Hilgard for the PET-PEESE code in assignment 4.3, Matti Heino for the GRIM test example in lecture 4.3, and Michelle Nuijten for feedback on assignment 4.4. Thanks to Seth Green, Russ Zack and Xu Fei at Code Ocean for help in using their platform to make it possible to run the R code online. I am extremely grateful for all alpha testers who provided feedback on early versions of the assignments: Daniel Dunleavy, Robert Gorsch, Emma Henderson, Martine Jansen, Niklas Johannes, Kristin Jankowsky, Cian McGinley, Robert Görsch, Chris Noone, Alex Riina, Burak Tunca, Laura Vowels, and Lara Warmelink, as well as the beta-testers who gave feedback on the material on Coursera: Johannes Breuer, Marie Delacre, Fabienne Ennigkeit, Marton L. Gy, and Sebastian Skejø. Finally, thanks to my wife for buying me six new shirts because ‘your audience has expectations’ (and for accepting how I worked through the summer holiday to complete this MOOC).
All material in the MOOC is shared with a CC-BY-NC-SA license, and you can access all material in the MOOC for free (and use it in your own education). Improving Your Statistical Questions is available from today. I hope you enjoy it!

Improving Education about P-values

A recent paper in AMPPS points out that many textbooks for introduction to psychology courses incorrectly explain p-values. There are dozens, if not hundreds, of papers that point out problems in how people understand p-values. If we don’t do anything about it, there will be dozens of articles like this in the next decades as well. So let’s do something about it.
When I made my first MOOC three years ago I spent some time thinking about how to explain what a p-value is clearly (you can see my video here). Some years later I realized that if you want to prevent misunderstandings of p-values, you should also explicitly train people about what p-values are not. Now, I think that training away misconceptions is just as important as explaining the correct interpretation of a p-value. Based on a blog post I made a new assignment for my MOOC. In the last year Arianne Herrera-Bennett (@ariannechb) performed an A/B test in my MOOC ‘Improving Your Statistical Inferences’. Half of the learners received this new assignment, explicitly aimed at training away misconceptions. The results are in her PhD thesis that she will defend on the 27th of September, 2019, but one of the main conclusions in the study is that it is possible to substantially reduce common misconceptions about p-values by educating people about them. This is a hopeful message.
I tried to keep the assignment as short as possible, and therefore it is 20 pages. Let that sink in for a moment. How much space does education about p-values take up in your study material? How much space would you need to prevent misunderstandings? And how often would you need to repeat the same material across the years? If we honestly believe misunderstanding of p-values are a problem, then why don’t we educate people well enough to prevent misunderstandings? The fact that people do not understand p-values is not their mistake – it is ours.
In my own MOOC I needed 7 pages to explain what p-value distributions look like, how they are a function of power, why p-values are uniformly distributed when the null is true, and what Lindley’s paradox is. But when I tried to clearly explain common misconceptions, I needed a lot more words. Before you want to blame that poor p-value, let me tell you that I strongly believe the problem of misconceptions is not limited to p-values: Probability is just not intuitive. It might always take more time to explain ways you can misunderstand something, than to teach the correct way to understand something.
In a recent pre-print I wrote on p-values, I reflect on the bad job we have been doing at teaching others about p-values. I write:
If anyone seriously believes the misunderstanding of p-values lies at the heart of reproducibility issues in science, why are we not investing more effort to make sure misunderstandings of p-values are resolved before young scholars perform their first research project? Although I am sympathetic to statisticians who think all the information researchers need to educate themselves on this topic is already available, as an experimental psychologist who works at a Human-Technology Interaction department this reminds me too much of the engineer who argues all the information to understand the copy machine is available in the user manual. In essence, the problems we have with how p-values are used is a human factors problem (Tryon, 2001). The challenge is to get researchers to improve the way they work.
Looking at the deluge of papers published in the last half century that point out how researchers have consistently misunderstood p-values, I am left to wonder: Where is the innovative coordinated effort to create world class educational materials that can freely be used in statistical training to prevent such misunderstandings? It is nowadays relatively straightforward to create online apps where people can simulate studies and see the behavior of p-values across studies, which can easily be combined with exercises that fit the knowledge level of bachelor and master students. The second point I want to make in this article is that a dedicated attempt to develop evidence based educational material in a cross-disciplinary team of statisticians, educational scientists, cognitive psychologists, and designers seems worth the effort if we really believe young scholars should understand p-values. I do not think that the effort statisticians have made to complain about p-values is matched with a similar effort to improve the way researchers use p-values and hypothesis tests. We really have not tried hard enough.
So how about we get serious about solving this problem? Let’s get together and make a dent in this decade old problem. Let’s try hard enough.
A good place to start might be to take stock of good ways to educate people about p-values that already exist, and then all together see how we can improve them.
I have uploaded my lecture about p-values to YouTube, and my assignment to train away misconceptions is available online as a Google Doc (the answers and feedback is here).
This is just my current approach to teaching p-values. I am sure there are many other approaches (and it might turn out that watching several videos, each explaining p-values in slightly different ways, is an even better way to educate people than having only one video). If anyone wants to improve this material (or replace it by better material) I am willing to open up my online MOOC for anyone who wants to do an A/B test of any good idea, so you can collect data from hundreds of students each year. I’m more than happy to collect best practices in p-value education – if you have anything you think (or have empirically shown) works well, send it my way – and make it openly available. Educators, pedagogists, statisticians, cognitive psychologists, software engineers, and designers interested in improving educational materials should find a place to come together. I know there are organizations that exist to improve statistics education (but have no good information about what they do, or which one would be best to join given my goals), and if you work for such an organization and are interested in taking p-value education to the next level, I’m more than happy to spread this message in my network and work with you.
If we really consider the misinterpretation of p-values to be one of the more serious problems underlying the lack of replicability of scientific findings, we need to seriously reflect on whether we have done enough to prevent misunderstandings. Treating it as a human factors problem might illuminate ways in which statistics education and statistical software can be improved. Let’s beat swords into ploughshares, and turn papers complaining about how people misunderstand p-values into papers that examine how we can improve education about p-values.

Requiring high-powered studies from scientists with resource constraints

This blog post is now included in the paper “Sample size justification” available at PsyArXiv. 

Underpowered studies make it very difficult to learn something useful from the studies you perform. Low power means you have a high probability of finding non-significant results, even when there is a true effect. Hypothesis tests which high rates of false negatives (concluding there is nothing, when there is something) become a malfunctioning tool. Low power is even more problematic combined with publication bias (shiny app). After repeated warnings over at least half a century, high quality journals are starting to ask authors who rely on hypothesis tests to provide a sample size justification based on statistical power.
The first time researchers use power analysis software, they typically think they are making a mistake, because the sample sizes required to achieve high power for hypothesized effects are much larger than the sample sizes they collected in the past. After double checking their calculations, and realizing the numbers are correct, a common response is that there is no way they are able to collect this number of observations.
Published articles on power analysis rarely tell researchers what they should do if they are hired on a 4 year PhD project where the norm is to perform between 4 to 10 studies that can cost at most 1000 euro each, learn about power analysis, and realize there is absolutely no way they will have the time and resources to perform high-powered studies, given that an effect size estimate from an unbiased registered report suggests the effect they are examining is half as large as they were led to believe based on a published meta-analysis from 2010. Facing a job market that under the best circumstances is a nontransparent marathon for uncertainty-fetishists, the prospect of high quality journals rejecting your work due to a lack of a solid sample size justification is not pleasant.
The reason that published articles do not guide you towards practical solutions for a lack of resources, is that there are no solutions for a lack of resources. Regrettably, the mathematics do not care about how small the participant payment budget is that you have available. This is not to say that you can not improve your current practices by reading up on best practices to increase the efficiency of data collection. Let me give you an overview of some things that you should immediately implement if you use hypothesis tests, and data collection is costly.
1) Use directional tests where relevant. Just following statements such as ‘we predict X is larger than Y’ up with a logically consistent test of that claim (e.g., a one-sided t-test) will easily give you an increase of 10% power in any well-designed study. If you feel you need to give effects in both directions a non-zero probability, then at least use lopsided tests.
2) Use sequential analysis whenever possible. It’s like optional stopping, but then without the questionable inflation of the false positive rate. The efficiency gains are so great that, if you complain about the recent push towards larger sample sizes without already having incorporated sequential analyses, I will have a hard time taking you seriously.
3) Increase your alpha level. Oh yes, I am serious. Contrary to what you might believe, the recommendation to use an alpha level of 0.05 was not the sixth of the ten commandments – it is nothing more than, as Fisher calls it, a ‘convenient convention’. As we wrote in our Justify Your Alpha paper as an argument to not require an alpha level of 0.005: “without (1) increased funding, (2) a reward system that values large-scale collaboration and (3) clear recommendations for how to evaluate research with sample size constraints, lowering the significance threshold could adversely affect the breadth of research questions examined.” If you *have* to make a decision, and the data you can feasibly collect is limited, take a moment to think about how problematic Type 1 and Type 2 error rates are, and maybe minimize combined error rates instead of rigidly using a 5% alpha level.
4) Use within designs where possible. Especially when measurements are strongly correlated, this can lead to a substantial increase in power.
5) If you read this blog or follow me on Twitter, you’ll already know about 1-4, so let’s take a look at a very sensible paper by Allison, Allison, Faith, Paultre, & Pi-Sunyer from 1997: Power and money: Designing statistically powerful studies while minimizing financial costs (link). They discuss I) better ways to screen participants for studies where participants need to be screened before participation, II) assigning participants unequally to conditions (if the control condition is much cheaper than the experimental condition, for example), III) using multiple measurements to increase measurement reliability (or use well-validated measures, if I may add), and IV) smart use of (preregistered, I’d recommend) covariates.
6) If you are really brave, you might want to use Bayesian statistics with informed priors, instead of hypothesis tests. Regrettably, almost all approaches to statistical inferences become very limited when the number of observations is small. If you are very confident in your predictions (and your peers agree), incorporating prior information will give you a benefit. For a discussion of the benefits and risks of such an approach, see this paper by van de Schoot and colleagues.
Now if you care about efficiency, you might already have incorporated all these things. There is no way to further improve the statistical power of your tests, and by all plausible estimates of effects sizes you can expect or the smallest effect size you would be interested in, statistical power is low. Now what should you do?
What to do if best practices in study design won’t save you?
The first thing to realize is that you should not look at statistics to save you. There are no secret tricks or magical solutions. Highly informative experiments require a large number of observations. So what should we do then? The solutions below are, regrettably, a lot more work than making a small change to the design of your study. But it is about time we start to take them seriously. This is a list of solutions I see – but there is no doubt more we can/should do, so by all means, let me know your suggestions on twitter or in the comments.
1) Ask for a lot more money in your grant proposals.
Some grant organizations distribute funds to be awarded as a function of how much money is requested. If you need more money to collect informative data, ask for it. Obviously grants are incredibly difficult to get, but if you ask for money, include a budget that acknowledges that data collection is not as cheap as you hoped some years ago. In my experience, psychologists are often asking for much less money to collect data than other scientists. Increasing the requested funds for participant payment by a factor of 10 is often reasonable, given the requirements of journals to provide a solid sample size justification, and the more realistic effect size estimates that are emerging from preregistered studies.
2) Improve management.
If the implicit or explicit goals that you should meet are still the same now as they were 5 years ago, and you did not receive a miraculous increase in money and time to do research, then an update of the evaluation criteria is long overdue. I sincerely hope your manager is capable of this, but some ‘upward management’ might be needed. In the coda of Lakens & Evers (2014) we wrote “All else being equal, a researcher running properly powered studies will clearly contribute more to cumulative science than a researcher running underpowered studies, and if researchers take their science seriously, it should be the former who is rewarded in tenure systems and reward procedures, not the latter.” and “We believe reliable research should be facilitated above all else, and doing so clearly requires an immediate and irrevocable change from current evaluation practices in academia that mainly focus on quantity.” After publishing this paper, and despite the fact I was an ECR on a tenure track, I thought it would be at least principled if I sent this coda to the head of my own department. He replied that the things we wrote made perfect sense, instituted a recommendation to aim for 90% power in studies our department intends to publish, and has since then tried to make sure quality, and not quantity, is used in evaluations within the faculty (as you might have guessed, I am not on the job market, nor do I ever hope to be).
3) Change what is expected from PhD students.
When I did my PhD, there was the assumption that you performed enough research in the 4 years you are employed as a full-time researcher to write a thesis with 3 to 5 empirical chapters (with some chapters having multiple studies). These studies were ideally published, but at least publishable. If we consider it important for PhD students to produce multiple publishable scientific articles during their PhD’s, this will greatly limit the types of research they can do. Instead of evaluating PhD students based on their publications, we can see the PhD as a time where researchers learn skills to become an independent researcher, and evaluate them not based on publishable units, but in terms of clearly identifiable skills. I personally doubt data collection is particularly educational after the 20th participant, and I would probably prefer to  hire a post-doc who had well-developed skills in programming, statistics, and who broadly read the literature, then someone who used that time to collect participant 21 to 200. If we make it easier for PhD students to demonstrate their skills level (which would include at least 1 well written article, I personally think) we can evaluate what they have learned in a more sensible manner than now. Currently, difference in the resources PhD students have at their disposal are a huge confound as we try to judge their skill based on their resume. Researchers at rich universities obviously have more resources – it should not be difficult to develop tools that allow us to judge the skills of people where resources are much less of a confound.
4) Think about the questions we collectively want answered, instead of the questions we can individually answer.
Our society has some serious issues that psychologists can help address. These questions are incredibly complex. I have long lost faith in the idea that a bottom-up organized scientific discipline that rewards individual scientists will manage to generate reliable and useful knowledge that can help to solve these societal issues. For some of these questions we need well-coordinated research lines where hundreds of scholars work together, pool their resources and skills, and collectively pursuit answers to these important questions. And if we are going to limit ourselves in our research to the questions we can answer in our own small labs, these big societal challenges are not going to be solved. Call me a pessimist. There is a reason we resort to forming unions and organizations that have to goal to collectively coordinate what we do. If you greatly dislike team science, don’t worry – there will always be options to make scientific contributions by yourself. But now, there are almost no ways for scientists who want to pursue huge challenges in large well-organized collectives of hundreds or thousands of scholars (for a recent exception that proves my rule by remaining unfunded: see the Psychological Science Accelerator). If you honestly believe your research question is important enough to be answered, then get together with everyone who also thinks so, and pursue answeres collectively. Doing so should, eventually (I know science funders are slow) also be more convincing as you ask for more resources to do the resource (as in point 1).
If you are upset that as a science we lost the blissful ignorance surrounding statistical power, and are requiring researchers to design informative studies, which hits substantially harder in some research fields than in others: I feel your pain. I have argued against universally lower alpha levels for you, and have tried to write accessible statistics papers that make you more efficient without increasing sample sizes. But if you are in a research field where even best practices in designing studies will not allow you to perform informative studies, then you need to accept the statistical reality you are in. I have already written too long a blog post, even though I could keep going on about this. My main suggestions are to ask for more money, get better management, change what we expect from PhD students, and self-organize – but there is much more we can do, so do let me know your top suggestions. This will be one of the many challenges our generation faces, but if we manage to address it, it will lead to a much better science.

Calculating Confidence Intervals around Standard Deviations

Power analyses require accurate estimates of the standard deviation. In this blog, I explain how to calculate confidence intervals around standard deviation estimates obtained from a sample, and show how much sample sizes in an a-priori power analysis can differ based on variation in estimates of the standard deviation.
If we calculate a standard deviation from a sample, this value is an estimate of the true value in the population. In small samples, our estimate can be quite far off, while due to the law of large numbers, as our sample size increases, we will be measuring the standard deviation more accurately. Since the sample standard deviation is an estimate with uncertainty, we can calculate a 95% confidence interval around it.
Expressing the uncertainty in our estimate of the standard deviation can be useful. When researchers plan to simulate data, or perform an a-priori power analysis, they need accurate estimates of the standard deviation. For simulations, the standard deviation needs to be accurate because we want to generate data that will look like the real data we will eventually collect. For power analyses we often want to think about the smallest effect size of interest, which can be specified as the difference in means you care about. To perform a power analysis we also need to specify the expected standard deviation of the data. Sometimes researchers will use pilot data to get an estimate of the standard deviation. Since the estimate of the population standard deviation based on a pilot study has some uncertainty, the width of confidence intervals around the standard deviation might be a useful way to show how much variability one can expect.
Below is the R code to calculate the confidence interval around a standard deviation from a sample, but you can also use this free GraphPad calculator. The R code then calculates an effect size based on a smallest effect size of interest of half a scale point (0.5) for a scale that has a true standard deviation of 1. The 95% confidence interval for the standard deviation based on a sample of 100 observation ranges from 0.878 to 1.162. If we draw a sample of 100 observations and happen to observe a value on the lower or upper bound of the 95% CI the effect size we calculate will be a Cohen’s d of 0.5/0.878 = 0.57 or 0.5/1.162 = 0.43. This is quite a difference in the effect size we might use for a power calculation. If we enter these effect size estimates in an a-priori power analysis where we aim to get 90% power using an alpha of 0.05 we will estimate that we need either 66 participants in each group, or 115 participants in each group.
It is clear sample sizes from a-priori power anayses depend strongly on an accurate estimate of the standard deviation. Keep into account that estimates of the standard deviation have uncertainty. Use validated or existing measures for which accurate estimates of the standard deviation in your population of interest are available, so that you can rely on a better estimate of the standard deviation in power analyses.
Some people argue that if you have such a limited understanding of the measures you are using that you do not even know the standard deviation of the measure in your population of interest, you are not ready to use that measure to test a hypothesis. If you are doing a power analysis but realize you have no idea what the standard deviation is, maybe you first need to spend more time validating the measures you are using.
When performing simulations or power analyses the same cautionary note can be made for estimates of correlations between dependent variables. When you are estimating these values from a sample, and want to perform simulations and/or power analyses, be aware that all estimates have some uncertainty. Try to get as accurate estimates as possible from pre-existing data. If possible, be a bit more conservative in sample size calculations based on estimated parameters, just to be sure.