There are 13 ways to analyse a replication study, but only one of them is coherent.

Paul Simon’s says there are 50 ways to leave your lover, and a similar abundance characterizes the contemporary literature on how to analyse a replication study. The recent SCORE replication project in Nature makes this explicit by reporting “13 replication success metrics along with the number of papers to which each metric could be applied” (Tyner et al., 2026). The reason for this, as the authors note, is that “No singular success metric has been accepted as optimal and universally applicable in the literature.” With so many approaches to choose from, it should not be a surprise that the inferences based on the studies vary substantially. As the authors report: “Thirteen methods for evaluating replication success provided estimates ranging from 28.6% to 74.8% (median of 49.3%).”

Fig. 1 from the SCORE project, with 13 ways to analyze a replication study.

Although it is understandable for such a massive project to refrain from strongly opinionated choices, I think we can all agree that we do not want to compute a median for different approaches to analyse replication success, and just like we don’t want 13 ways to analyse an original study, we don’t want 13 ways to analyse a replication study. The current state of how to analyse replication studies is not as much an embarrassment of riches, but an embarrassment of a lack of a coherent epistemology. In science, we don’t compute statistics just because we can. We compute statistics because they help us to generate knowledge. In my experience, in science no “singular” anything is ever “accepted” – and especially not an approach to statistical inferences (as the ever-ongoing disagreement between Bayesians and Frequentists illustrates). Instead of waiting for agreement, we should think about which approach to the analysis of a replication study coherently follows from our epistemology.

Two metrics do the bulk of the epistemic work in the replication project. The authors are explicit that “Primary reporting emphasizes the two most reported replication metrics: statistical significance and effect size comparisons.” The authors are right to focus on these two measures, as these two inferences – whether the p-value is significant, and whether the effect sizes are similar – reflect what researchers treat as substantive claims in studies. In our recent paper ‘How to analyse a replication study’ we point out that these two inferences are directly related to basic statements that scientists make: whether the same ordinal decision can be made in the replication, and whether the magnitude of the effect meaningfully corresponds to the original estimate (Lakens et al., 2026).

While the authors understandably do not make too strong a point about their focus on 2 of the 13 metrics, their decision is not just based on which measures are commonly reported but also based on an epistemically coherent approach to the analysis of a replication study. Replication projects like SCORE are unmistakably designed within a methodological falsificationist framework, even when this philosophical background is not mentioned explicitly. In a falsificationist framework, which is implemented thought the Neyman-Pearson approach to statistical inferences, error rates are tightly controlled, and claims are made based on the results of a hypothesis test. It is clear the score authors followed a methodological falsificationist framework and the Neyman-Pearson approach to statistics as they preregistered (allowing others to evaluate how severely they controlled their error rates), designed studies with high statistical power, and set a prespecified alpha level.

From our perspective, the central goal of a replication study is not to ask a new statistical question, but to revisit the same question as in the original study, after collecting new data. As we argue, “the goal of a replication study is to examine whether the same basic statement that was made in an original study can also be made when new data are collected in a faithful empirical realization of the original test.” Within a methodological falsificationist framework, original findings enter the literature as tentative basic statements, justified by a statistical decision rule with known error rates. Replication studies function as a critical check on whether such statements were merely the result of a Type I error. As we note, “one of the main functions of a replication study is to determine the stability of a finding, which should not be present if the original finding was a Type I error.” Even though replications inevitably change many auxiliary conditions—because, as Popper already observed, experiments can never be repeated exactly—this does not undermine their epistemic role. Instead, replications test whether the original claim survives variation in factors that were implicitly relegated to the ceteris paribus clause, thereby probing whether the original inference was robust or not.

This view has direct implications for how replication studies should be analysed. If original claims were made by rejecting a null hypothesis at a prespecified alpha level, then “the replication study should evaluate whether the same claim can be made using the same inferential criterion.” And if researchers also treated the original effect size estimate as part of the claim (which they seem to do in practice) then replication studies must additionally examine whether effect sizes differ meaningfully. While the other eleven approaches to assessing replication success are statistically legitimate and can certainly be reported, they answer different questions and rest on different epistemic commitments. The coherent approach is the one that aligns epistemological aims, philosophy of science, and statistical procedure. Statistics follow from the questions we ask, the questions we ask follow from our philosophy of science, and without such coherence we cannot have a principled approach to the analysis of replication studies. Maybe it is time to admit that there are 13 statistical quantities that can be computed for a replication study, but there is really only one way to do so coherently from a specific philosophy of scientific knowledge generation.

 

References

Lakens, D., Leach, N. M., Haans, A., Uygun Tunç, D., & Tunç, M. N. (2026). How to analyze a replication study. PsyArXiv. https://osf.io/preprints/psyarxiv/7ydgu_v1/ 

Tyner, A. H., Abatayo, A. L., Daley, M., Field, S., Fox, N., Haber, N. A., Hahn, K. M., Struhl, M. K., Mawhinney, B., Miske, O., Silverstein, P., Soderberg, C. K., Stankov, T., Abbasi, A., Aberson, C. L., Aczel, B., Adamkovič, M., Albayrak, N., Allen, P. J., … Errington, T. M. (2026). Investigating the replicability of the social and behavioural sciences. Nature, 652(8108), 143–150. https://doi.org/10.1038/s41586-025-10078-y

Type S and M errors as a “rhetorical tool”

Update 30/09/2025: I have added a reply by Andrew Gelman below my original blog post. 

We recently posted a preprint criticizing the idea of Type S and M errors (https://osf.io/2phzb_v1). From our abstract: “While these concepts have been proposed to be useful both when designing a study (prospective) and when evaluating results (retroactive), we argue that these statistics do not facilitate the proper design of studies, nor the meaningful interpretation of results.”

In a recent blog post that is mainly on p-curve analysis, Gelman writes briefly about Type S and M errors, stating that he does not see them as tools that should be used regularly, but that they mainly function as a ‘rhetorical tool’:

I offer a three well-known examples of statistical ideas arising in the field of science criticism, three methods whose main value is rhetorical:

[…]

2. The concepts of Type M and Type S errors, which I developed with Francis Tuerlinckx in 2000 and John Carlin in 2014. This has been an influential idea–ok, not as influential as Ioannidis’s paper!–and I like it a lot, but it doesn’t correspond to a method that I will typically use in practice. To me, the value of the concepts of Type M and Type S errors is they help us understand certain existing statistical procedures, such as selection on statistical significance, that have serious problems. There’s mathematical content here for sure, but I fundamentally think of these error calculations as having rhetorical value for the design of studies and interpretation of reported results.

The main sentence of interest here is that Gelman says this is not a method he would use in practice. I was surprised, because in their article Gelman and Carlin (2014) recommend the calculation of Type S and M errors more forcefully: “We suggest that design calculations be performed after as well as before data collection and analysis.” Throughout their article, they compare design calculations where Type S and M errors are calculated to power analyses, which are widely seen as a requirement before data collection of any hypothesis testing study. For example, in the abstract they write “power analysis is flawed in that a narrow emphasis on statistical significance is placed as the primary focus of study design. In noisy, small-sample settings, statistically significant results can often be misleading. To help researchers address this problem in the context of their own studies, we recommend design calculations”.

They also say design calculations are useful when interpreting results, and that they add something to p-values and effect sizes, which again seems to suggest they can complement ordinary data analysis: “Our retrospective analysis provided useful insight, beyond what was revealed by the estimate, confidence interval, and p value that came from the original data summary.” (Gelman & Carlin, 2014, p. 646). In general, they seem to suggest design analyses are done before or after data analysis: “First, it is indeed preferable to do a design analysis ahead of time, but a researcher can analyze data in many different ways—indeed, an important part of data analysis is the discovery of unanticipated patterns (Tukey, 1977) so that it is unreasonable to suppose that all potential analyses could have been determined ahead of time. The second reason for performing postdata design calculations is that they can be a useful way to interpret the results from a data analysis, as we next demonstrate in two examples.” (Gelman & Carlin, 2014, p. 643).

One the other hand, in a single sentence in the discussion, they also write: “Our goal in developing this software is not so much to provide a tool for routine use but rather to demonstrate that such calculations are possible and to allow researchers to play around and get a sense of the sizes of Type S errors and Type M errors in realistic data settings.”

Maybe I have always misinterpreted Gelman and Carlin, 2014, in that I took it as a paper that recommended the regular use of Type S and M errors, and I should have understood that the sentence in the discussion made it clear that this was never their intention. If the idea is to replace Type 1 and 2 errors, and hence, replace power analysis and the interpretation of data, design analysis should be part of every hypothesis testing study. Sentences such as “the requirement of design analysis can stimulate engagement with the existing literature in the subject-matter field” seemed to suggest to me that design analyses could be a requirement for all studies. But maybe I was wrong.

 

Or maybe I wasn’t.

 

In this blog post, Gelman writes: “Now, one odd thing about my paper with Carlin is that it gives some tools that I recommend others use when designing and evaluating their research, but I would not typically use these tools directly myself! Because I am not wanting to summarize inference by statistical significance.” So, here there seems to be the idea that others routinely use Type S and M errors. And in a very early version of the paper with Carlin, available here, the opening sentence also suggests routine use: “The present article proposes an ideal that every statistical analysis be followed up with a power calculation to better understand the inference from the data. As the quotations above illustrate, however, our suggestion contradicts the advice of many respected statisticians. Our resolution of this apparent disagreement is that we perform retrospective power analysis in a different way and for a different purpose than is typically recommended in the literature.”

Of course, one good thing about science is that people change their beliefs about things. Maybe Gelman one time thought Type S and M errors should be part of ‘every statistical analysis’ but now sees the tool mainly as a ‘rhetorical device’. And that is perfectly fine. It is also good to know, because I regular see people who suggest that Type S and M error should routinely be used in practice. I guess I can now point them to a blog post where Gelman himself disagrees with that suggestion.

As we explain in our preprint, the idea of Type S errors is conceptually incoherent, and any probabilities calculated will be identical to the Type 1 error in directional tests, or the false discovery rate, as all that Type S errors do is remove the possibility of an effect being 0 from the distribution, but this probability is itself 0. We also explain how other tools are better to educate researchers about effect size inflation in studies selected for significance (for which Gelman would recommend Type M errors), and we actually recommend p-uniform for this, or just teaching people about critical effect sizes.

Personally, I don’t like rhetorical tools. Although in our preprint we agree that teaching the idea of Type S and M errors can be useful in education, there are also conceptually coherent and practically useful statistical ideas that we can teach instead to achieve the same understanding. Rhetorical tools might be useful to convince people who do not think logically about a topic, but I prefer to have a slightly higher bar for the scientists that I aim to educate about good research practices, and I think they are able to understand the problem of low statistical power and selection bias without rhetorical tools.

--Reply by Andrew Gelman--

Hi, Daniel.  Thanks for your comments.  It's always good to see that people are reading our articles and blog posts.  I think you are a little bit confused about what we wrote, but ultimately that's our fault for not being clear, so I appreciate the opportunity to clarify.

So you don't need to consider this comment as a "rebuttal" to your post.  For convenience I'll go through several of your statements one by one, but my goal is to clarify.

First, I guess I should've avoided the word "rhetorical."  In my post, I characterized Ioannidis's 2005 claim, type M and S errors, and multiverse analysis as "rhetorical tools" that have been been useful in the field of science criticism but which I would not use in my own analyses.  I could've added to this many other statistical methods including p-values and Bayes factors.

When I describe a statistical method as "rhetorical" in this context, I'm not saying it's mathematically invalid or that it's conceptually incoherent (to use your term), nor am I saying these methods should not be used!  All these tools can be useful; they just rely on very strong assumptions.  P-values and Bayes factors are measures of evidence relative to a null hypothesis (not just an assumption that a particular parameter equals zero, but an entire set of assumptions about the data-generating process) that is irrelevant in the science and decision problems I've seen--but these methods are clearly defined and theoretically justified, and many practitioners get a lot out of them.  I very rarely would use p-values or Bayes factors in my work because I'm very rarely interested in this sort of discrepancy from a null hypothesis.

A related point comes up in my paper with Hill and Yajima, "Why we (usually) don't have to worry about multiple comparisons" (https://sites.stat.columbia.edu/gelman/research/published/multiple2f.pdf).  Multiple comparisons corrections can be important, indeed I've criticized some published work for misinterpreting evidence by not accounting for multiple comparisons or multiple potential comparisons--but it doesn't come up so much in the context of multilevel modeling.

Ioannidis (2005) is a provocative paper that I think has a lot of value--but you have to be really careful to try to directly apply such an analysis to real data.   He's making some really strong assumptions!  The logic of his paper is clear, though.  O'Rourke and I discuss the challenges of moving from that sort of model to larger conclusions in our 2013 paper (https://sites.stat.columbia.edu/gelman/research/published/GelmanORourkeBiostatistics.pdf).

The multiverse is a cool idea, and researchers have found it to be useful.  The sociologists Cristobal Young and Erin Cumberworth recently published a book on it (https://www.cambridge.org/core/books/multiverse-analysis/D53C3AB449F6747B4A319174E5C95FA1).  I don't think I'd apply the method in my own applied research, though, because the whole idea of the multiverse is to consider all the possible analyses you might have done on a dataset, and if I get to that point I'm more inclined to fit a multilevel model that subsumes all these analyses.  I have found multiverse analysis to be useful in understanding research published by others, and maybe it would be useful for my own work too, given that my final published analyses never really include all the possibilities of what I might have done.  The point is that this is yet another useful method that can have conceptual value even if I might not apply it to my own work.  Again, the term "rhetorical" might be misleading, as these are real methods that, like all statistical methods, are appropriate in some settings and not in others.

So please don't let your personal dislike of the term "rhetorical tools" to dissuade you from taking seriously the tools that I happen to have characterized as "rhetorical," as these include p-values, multiple comparisons corrections, Bayesian analysis with point priors, and all sorts of other methods that are rigorously defined and can be useful in many applied settings, including some of yours!

OK, now on to Type M and Type S errors.  You seem to imply that at some time I thought that these "should be part of ‘every statistical analysis,'" but I can assure you that I have never believed or written such a thing.  You put the phrase "every statistical analysis," but this is your phrase, not mine.

One very obvious way to see that I never thought Type M and Type S errors "should be part of ‘every statistical analysis'" is that, since the appearance of that article in 2014, I've published dozens of applied papers, and in only very few of these did I look at Type M and Type S errors.

What is that?  Why is it that my colleagues and I came up with this idea that has been influential, and which I indeed think can be very useful and which I do think should often be used by practitioners, but I only use it myself?

The reason is that the focus of our work on Type M and Type S errors has been to understand selection on statistical significance (as in that notorious estimate that early childhood intervention increases adult earnings by 42% on average, but with that being the result of an inferential procedure that, under any reasonable assumptions, greatly overestimates the magnitude of any real effect; that is, Type M error).  In my applied work it's very rare that I condition on statistical significance, and so this sort of use of Type M and S errors is not so relevant.  So it's perfectly coherent for me to say that Type M and S error analysis is valuable in a wide range of settings that that I think these tools should be applied very widely, without believing that they should be part of "every statistical analysis" or that I should necessarily use them for my own analyses.

That said, more recently I've been thinking that Type M and S errors are a useful approach to understanding statistical estimates more generally, not just for estimates that are conditioned on statistical significance.  I'm working with Erik van Zwet and Witold Więcek on applying these ideas to Bayesian inferences as well.  So I'm actually finding these methods to be more, not less, valuable for statistical understanding, and not just for "people who do not think logically about a topic" (in your phrasing).  Our papers on these topics are published in real journals and of course they're intended for people who <em>do</em> think logically about the topic!  And, just to be clear, I believe that you're thinking logically in your post too; I just think you've been misled by my terminology (again, I accept the blame for that), and also you work on different sorts of problems than I do, so it makes sense that a method that I find useful might not be so helpful to you.  There are many ways to Rome, which is another point I was making in that blog post.

Finally, a few things in your post that I did not address above:

1.  You quote from my blog post, where I wrote, “Now, one odd thing about my paper with Carlin is that it gives some tools that I recommend others use when designing and evaluating their research, but I would not typically use these tools directly myself! Because I am not wanting to summarize inference by statistical significance.”  That's exactly my point above!  You had it right there.

2.  You wrote, "Maybe I have always misinterpreted Gelman and Carlin, 2014, in that I took it as a paper that recommended the regular use of Type S and M errors, and I should have understood that the sentence in the discussion made it clear that this was never their intention."  So, just to clarify, yes in our paper we recommended the regular use of Type M and S errors, and we still recommend that!

3.  You write that our "sentences such as 'the requirement of design analysis can stimulate engagement with the existing literature in the subject-matter field' seemed to suggest to me that design analyses could be a requirement for all studies."  That's right--I actually do think that design analysis should be done for all studies!

OK, nothing is done all the time.  I guess that some studies are so cheap that there's no need for a design analysis--or maybe we could say that in such studies the design analysis is implicit.  For example, if I'm doing A/B testing in a company, and they've done lots of A/B tests before, and I think the new effect will be comparable to previous things being studied, then maybe I just go with the same design as in previous experiments, without performing a formal design analysis.  But one could argue that this corresponds to some implicit calculation.

In any case, yeah, in general I think that a design analysis should come before any study.  Indeed, that is what I tell students and colleagues:  never collect data before doing a simulation study first.  Often we do fake-data simulation after the data come in, to validate our model-fitting strategies, but for a while I've been thinking it's best to do it before.

This is not controversial advice in statistics, to recommend a design analysis before gathering data!  Indeed, in medical research it's basically a requirement.  In our paper, Carlin and I argue--and I still believe--that a design analysis using Type M and S errors is more valuable than the traditional Type 1 and 2 errors.  But in any case I consider "design analysis" to be the general term, with "power analysis" being a special case (design analysis looking at the probability of attaining statistical significance).  I don't think traditional power analysis is useless--one way you can see this is that we demonstrate power calculations in chapter 16 of Regression and Other Stories, a book that came out several years after my paper with Carlin--; I just think it can be misleading, especially if it is done without consideration of Type M and S errors.

Thanks again for your comments.  It's good to have an opportunity to clarify my thinking, and these are important issues in statistics.

P.S.  If you see something on our blog that you disagree with, feel free to comment there directly, as that way you can also reach readers of the original post.

--

References: 

Lakens, D., Cristian, Xavier-Quintais, G., Rasti, S., Toffalini, E., & Altoè, G. (2025). Rethinking Type S and M Errors. OSF. https://doi.org/10.31234/osf.io/2phzb_v1

Gelman, A., & Carlin, J. (2014). Beyond Power Calculations: Assessing Type S (Sign) and Type M (Magnitude) Errors. Perspectives on Psychological Science, 9(6), 641–651. https://doi.org/10.1177/1745691614551642

Tukey on Decisions and Conclusions

In 1955 Tukey gave a dinner talk about the difference between decisions and conclusions at a meeting of the Section of Physical and Engineering Science of the American Statistical Association. The talk was published in 1960. The distinction relates directly to different goals researchers might have when they collect data. This blog is largely a summary of his paper.

 

Tukey was concerned about the ‘tendency of decision theory to attempt to conquest all of statistics’. In hindsight, he needn’t have worried. In the social sciences, most statistics textbooks do not even discuss decision theory. His goal was to distinguish decisions from conclusions, to carve out a space for ‘conclusion theory’ to complement decision theory. He distinguishes decisions from conclusions.

 

In practice, making a decision means to ‘decide to act for the present as if’. Possible actions are defined, possible states of nature identified, and we make an inference about each state of nature. Decisions can be made even when we remain extremely uncertain about any ‘truth’. Indeed, in extreme cases we can even make decisions without access to any data. We might even decide to act as if two mutually exclusive states of nature are true! For example, we might buy a train ticket for a holiday three months from now, but also take out life insurance in case we die tomorrow.   

 

Conclusions differ from decisions. First, conclusions are established without taking consequences into consideration. Second, conclusions are used to build up a ‘fairly well-established body of knowledge’. As Tukey writes: “A conclusion is a statement which is to be accepted as applicable to the conditions of an experiment or observation unless and until unusually strong evidence to the contrary arises.” A conclusion is not a decision on how to act in the present. Conclusions are to be accepted, and thereby incorporated into what Frick (1996) calls a ‘corpus of findings’. According to Tukey, conclusions are used to narrow down the number of working hypotheses still considered consistent with observations. Conclusions should be reached, not based on their consequences, but because of their lasting (but not everlasting, as conclusions can now and then be overturned by new evidence) contribution to scientific knowledge.

 

Tests of hypotheses

 

According to Tukey, a test of hypotheses can have two functions. The first function is as a decision procedure, and the second function is to reach a conclusion. In a decision procedure the goal is to choose a course of action given an acceptable risk. This risk can be high. For example, a researcher might decide not to pursue a research idea after a first study, designed to have 80% power for a smallest effect size of interest, yields a non-significant result. The error rate is at most 20%, but the researcher might have enough good research ideas to not care.

 

The second function is to reach a conclusion. This is done, according to Tukey, by controlling the Type 1 and Type 2 error rate at ‘suitably low levels’ (Note: Tukey’s discussion of concluding an effect is absent is hindered somewhat by the fact that equivalence tests were not yet widely established in 1955 – Hodges & Lehman’s paper appeared in 1954). Low error rates, such as the conventions to use a 5% of 1% alpha level, are needed to draw conclusions that can enter the corpus of findings (even though some of these conclusions will turn out to be wrong, in the long run).

 

Why would we need conclusions?

 

One might reasonably wonder if we need conclusions in science. Tukey also ponders this question in Appendix 2. He writes “Science, in the broadest sense, is both one of the most successful of human affairs, and one of the most decentralized. In principle, each of us puts his evidence (his observations, experimental or not, and their discussion) before all the others, and in due course an adequate consensus of opinion develops.” He argues not for an epistemological reason, nor for a statistical reason, but for a sociological reason. Tukey writes: “There are four types of difficulty, then, ranging from communication through assessment to mathematical treatment, each of which by itself will be sufficient, for a long time, to prevent the replacement, in science, of the system of conclusions by a system based more closely on today’s decision theory.” He notes how scientists can no longer get together in a single room (as was somewhat possible in the early decades of the Royal Society of London) to reach consensus about decisions. Therefore, they need to communicate conclusions, as “In order to replace conclusions as the basic means of communication, it would be necessary to rearrange and replan the entire fabric of science.” 

 

I hadn’t read Tukey’s paper when we wrote our preprint “The Epistemic and Pragmatic Function of Dichotomous Claims Based on Statistical Hypothesis Tests”. In this preprint, we also discuss a sociological reason for the presence of dichotomous claims in science. We also ask: “Would it be possible to organize science in a way that relies less on tests of competing theories to arrive at intersubjectively established facts about phenomena?” and similarly conclude: “Such alternative approaches seem feasible if stakeholders agree on the research questions that need to be investigated, and methods to be utilized, and coordinate their research efforts”.  We should add a citation to Tukey's 1960 paper.

 

Is the goal of an study a conclusion, a decision, or both?

 

Tukey writes he “looks forward to the day when the history and status of tests of hypotheses will have been disentangled.” I think that in 2022 that day has not yet come. At the same time, Tukey admits in Appendix 1 that the two are sometimes intertwined.

 

A situation Tukey does not discuss, but that I think is especially difficult to disentangle, is a cumulative line of research. Although I would prefer to only build on an established corpus of findings, this is simply not possible. Not all conclusions in the current literature are reached with low error rates. This is true both for claims about the absence of an effect (which are rarely based on an equivalence test against a smallest effect size of interest with a low error rate), as for claims about the presence of an effect, not just because of p-hacking, but also because I might want to build on an exploratory finding from a previous study. In such cases, I would like to be able to conclude the effects I build on are established findings, but more often than not, I have to decide these effects are worth building on. The same holds for choices about the design of a set of studies in a research line. I might decide to include a factor in a subsequent study, or drop it. These decisions are based on conclusions with low error rates if I had the resources to collect large samples and perform replication studies, but other times they involve decisions about how to act in my next study with quite considerable risk.

 

We allow researchers to publish feasibility studies, pilot studies, and exploratory studies. We don’t require every study to be a Registered Report of Phase 3 trial. Not all information in the literature that we build on has been established with the rigor Tukey associates with conclusions. And the replication crisis has taught us that more conclusions from the past are later rejected than we might have thought based on the alpha levels reported in the original articles. And in some research areas, where data is scarce, we might need to accept that, if we want to learn anything, the conclusions will always more tentative (and the error rates accepted in individual studies will be higher) than in research areas where data is abundant.

 

Even if decisions and conclusions can not be completely disentangled, reflecting on their relative differences is very useful, as I think it can help us to clarify the goal we have when we collect data. 

 

For a 2013 blog post by Justin Esarey, who found the distinction a bit less useful than I found it, see https://polmeth.org/blog/scientific-conclusions-versus-scientific-decisions-or-we%E2%80%99re-having-tukey-thanksgiving

 

References

Frick, R. W. (1996). The appropriate use of null hypothesis testing. Psychological Methods, 1(4), 379–390. https://doi.org/10.1037/1082-989X.1.4.379

Tukey, J. W. (1960). Conclusions vs decisions. Technometrics, 2(4), 423–433.

Uygun Tunç, D., Tunç, M. N., & Lakens, D. (2021). The Epistemic and Pragmatic Function of Dichotomous Claims Based on Statistical Hypothesis Tests. PsyArXiv. https://doi.org/10.31234/osf.io/af9by

 

 

 

 

 

Not All Flexibility P-Hacking Is, Young Padawan

During a recent workshop on Sample Size Justification an early career researcher asked me: “You recommend sequential analysis in your paper for when effect sizes are uncertain, where researchers collect data, analyze the data, stop when a test is significant, or continue data collection when a test is not significant, and, I don’t want to be rude, but isn’t this p-hacking?”

In linguistics there is a term for when children apply a rule they have learned to instances where it does not apply: Overregularization. They learn ‘one cow, two cows’, and use the +s rule for plural where it is not appropriate, such as ‘one mouse, two mouses’ (instead of ‘two mice’). The early career researcher who asked me if sequential analysis was a form of p-hacking was also overregularizing. We teach young researchers that flexibly analyzing data inflates error rates, is called p-hacking, and is a very bad thing that was one of the causes of the replication crisis. So, they apply the rule ‘flexibility in the data analysis is a bad thing’ to cases where it does not apply, such as in the case of sequential analyses. Yes, sequential analyses give a lot of flexibility to stop data collection, but it does so while carefully controlling error rates, with the added bonus that it can increase the efficiency of data collection. This makes it a good thing, not p-hacking.

 

Children increasingly use correct language the longer they are immersed in it. Many researchers are not yet immersed in an academic environment where they see flexibility in the data analysis applied correctly. Many are scared to do things wrong, which risks becoming overly conservative, as the pendulum from ‘we are all p-hacking without realizing the consequences’ swings back to far to ‘all flexibility is p-hacking’. Therefore, I patiently explain during workshops that flexibility is not bad per se, but that making claims without controlling your error rate is problematic.

In a recent podcast episode of ‘Quantitude’ one of the hosts shared a similar experience 5 minutes into the episode. A young student remarked that flexibility during the data analysis was ‘unethical’. The remainder of the podcast episode on ‘researcher degrees of freedom’ discussed how flexibility is part of data analysis. They clearly state that p-hacking is problematic, and opportunistic motivations to perform analyses that give you what you want to find should be constrained. But they then criticized preregistration in ways many people on Twitter disagreed with. They talk about ‘high priests’ who want to ‘stop bad people from doing bad things’ which they find uncomfortable, and say ‘you can not preregister every contingency’. They remark they would be surprised if data could be analyzed without requiring any on the fly judgment.

Although the examples they gave were not very good¹ it is of course true that researchers sometimes need to deviate from an analysis plan. Deviating from an analysis plan is not p-hacking. But when people talk about preregistration, we often see overregularization: “Preregistration requires specifying your analysis plan to prevent inflation of the Type 1 error rate, so deviating from a preregistration is not allowed.” The whole point of preregistration is to transparently allow other researchers to evaluate the severity of a test, both when you stick to the preregistered statistical analysis plan, as when you deviate from it. Some researchers have sufficient experience with the research they do that they can preregister an analysis that does not require any deviations², and then readers can see that the Type 1 error rate for the study is at the level specified before data collection. Other researchers will need to deviate from their analysis plan because they encounter unexpected data. Some deviations reduce the severity of the test by inflating the Type 1 error rate. But other deviations actually get you closer to the truth. We can not know which is which. A reader needs to form their own judgment about this.

A final example of overregularization comes from a person who discussed a new study that they were preregistering with a junior colleague. They mentioned the possibility of including a covariate in an analysis but thought that was too exploratory to be included in the preregistration. The junior colleague remarked: “But now that we have thought about the analysis, we need to preregister it”. Again, we see an example of overregularization. If you want to control the Type 1 error rate in a test, preregister it, and follow the preregistered statistical analysis plan. But researchers can, and should, explore data to generate hypotheses about things that are going on in their data. You can preregister these, but you do not have to. Not exploring data could even be seen as research waste, as you are missing out on the opportunity to generate hypotheses that are informed by data. A case can be made that researchers should regularly include variables to explore (e.g., measures that are of general interest to peers in their field), as long as these do not interfere with the primary hypothesis test (and as long as these explorations are presented as such).

In the book “Reporting quantitative research in psychology: How to meet APA Style Journal Article Reporting Standards” by Cooper and colleagues from 2020 a very useful distinction is made between primary hypotheses, secondary hypotheses, and exploratory hypotheses. The first consist of the main tests you are designing the study for. The secondary hypotheses are also of interest when you design the study – but you might not have sufficient power to detect them. You did not design the study to test these hypotheses, and because the power for these tests might be low, you did not control the Type 2 error rate for secondary hypotheses. You can preregister secondary hypotheses to control the Type 1 error rate, as you know you will perform them, and if there are multiple secondary hypotheses, as Cooper et al (2020) remark, readers will expect “adjusted levels of statistical significance, or conservative post hoc means tests, when you conducted your secondary analysis”.

If you think of the possibility to analyze a covariate, but decide this is an exploratory analysis, you can decide to neither control the Type 1 error rate nor the Type 2 error rate. These are analyses, but not tests of a hypothesis, as any findings from these analyses have an unknown Type 1 error rate. Of course, that does not mean these analyses can not be correct in what they reveal – we just have no way to know the long run probability that exploratory conclusions are wrong. Future tests of the hypotheses generated in exploratory analyses are needed. But as long as you follow Journal Article Reporting Standards and distinguish exploratory analyses, readers know what the are getting. Exploring is not p-hacking.

People in psychology are re-learning the basic rules of hypothesis testing in the wake of the replication crisis. But because they are not yet immersed in good research practices, the lack of experience means they are overregularizing simplistic rules to situations where they do not apply. Not all flexibility is p-hacking, preregistered studies do not prevent you from deviating from your analysis plan, and you do not need to preregister every possible test that you think of. A good cure for overregularization is reasoning from basic principles. Do not follow simple rules (or what you see in published articles) but make decisions based on an understanding of how to achieve your inferential goal. If the goal is to make claims with controlled error rates, prevent Type 1 error inflation, for example by correcting the alpha level where needed. If your goal is to explore data, feel free to do so, but know these explorations should be reported as such. When you design a study, follow the Journal Article Reporting Standards and distinguish tests with different inferential goals.

 

¹ E.g., they discuss having to choose between Student’s t-test and Welch’s t-test, depending on wheter Levene’s test indicates the assumption of homogeneity is violated, which is not best practice – just follow R, and use Welch’s t-test by default.

² But this is rare – only 2 out of 27 preregistered studies in Psychological Science made no deviations. https://royalsocietypublishing.org/doi/full/10.1098/rsos.211037 We can probably do a bit better if we only preregistered predictions at a time where we really understand our manipulations and measures.

P-values vs. Bayes Factors

In the first partially in person scientific meeting I am attending after the COVID-19 pandemic, the Perspectives on Scientific Error conference in the Lorentz Center in Leiden, the organizers asked Eric-Jan Wagenmakers and myself to engage in a discussion about p-values and Bayes factors. We each gave 15 minute presentations to set up our arguments, centered around 3 questions: What is the goal of statistical inference, What is the advantage of your approach in a practical/applied context, and when do you think the other approach may be applicable?

 

What is the goal of statistical inference?

 

When browsing through the latest issue of Psychological Science, many of the titles of scientific articles make scientific claims. “Parents Fine-Tune Their Speech to Children’s Vocabulary Knowledge”, “Asymmetric Hedonic Contrast: Pain is More Contrast Dependent Than Pleasure”, “Beyond the Shape of Things: Infants Can Be Taught to Generalize Nouns by Objects’ Functions”, “The Bilingual Advantage in Children’s Executive Functioning is Not Related to Language Status: A Meta-Analysis”, or “Response Bias Reflects Individual Differences in Sensory Encoding”. These authors are telling you that if you take away one thing from the work the have been doing, it is a claim that some statistical relationship is present or absent. This approach to science, where researchers collect data to make scientific claims, is extremely common (we discuss this extensively in our preprint “The Epistemic and Pragmatic Function of Dichotomous Claims Based on Statistical Hypothesis Tests” by Uygun- Tunç, Tunç, & Lakens, https://psyarxiv.com/af9by/). It is not the only way to do science – there is purely descriptive work, or estimation, where researchers present data without making any claims beyond the observed data, so there is never a single goal in statistical inferences – but if you browse through scientific journals, you will see that a large percentage of published articles have the goal to make one or more scientific claims.

 

Claims can be correct or wrong. If scientists used a coin flip as their preferred methodological approach to make scientific claims, they would be right and wrong 50% of the time. This error rate is considered too high to make scientific claims useful, and therefore scientists have developed somewhat more advanced methodological approaches to make claims. One such approach, widely used across scientific fields, is Neyman-Pearson hypothesis testing. If you have performed a statistical power analysis when designing a study, and if you think it would be problematic to p-hack when analyzing the data from your study, you engaged in Neyman-Pearson hypothesis testing. The goal of Neyman-Pearson hypothesis testing is to control the maximum number of incorrect scientific claims the scientific community collectively makes. For example, when authors write “The Bilingual Advantage in Children’s Executive Functioning is Not Related to Language Status: A Meta-Analysis” we could expect a study design where people specified a smallest effect size of interest, and statistically reject the presence of any worthwhile effect of bilingual advantage in children on executive functioning based on language status in an equivalence test. They would make such a claim with a pre-specified maximum Type 1 error rate, or the alpha level, often set to 5%. Formally, authors are saying “We might be wrong, but we claim there is no meaningful effect here, and if all scientists collectively act as if we are correct about claims generated by this methodological procedure, we would be misled no more than alpha% of the time, which we deem acceptable, so let’s for the foreseeable future (until new data emerges that proves us wrong) assume our claim is correct”. Discussion sections are often less formal, and researchers often violate the code of conduct for research integrity by selectively publishing only those results that confirm their predictions, which messes up many of the statistical conclusions we draw in science.

 

The process of claim making described above does not depend on an individual’s personal beliefs, unlike some Bayesian approaches. As Taper and Lele (2011) write: “It is not that we believe that Bayes’ rule or Bayesian mathematics is flawed, but that from the axiomatic foundational definition of probability Bayesianism is doomed to answer questions irrelevant to science. We do not care what you believe, we barely care what we believe, what we are interested in is what you can show.” This view is strongly based on the idea that the goal of statistical inference is the accumulation of correct scientific claims through methodological procedures that lead to the same claims by all scientists who evaluate the tests of these claims. Incorporating individual priors into statistical inferences, and making claims dependent on their prior belief, does not provide science with a methodological procedure that generates collectively established scientific claims. Bayes factors provide a useful and coherent approach to update individual beliefs, but they are not a useful tool to establish collectively agreed upon scientific claims.

 

What is the advantage of your approach in a practical/applied context?

 

A methodological procedure built around a Neyman-Pearson perspective works well in a science where scientists want to make claims, but we want to prevent too many incorrect scientific claims. One attractive property of this methodological approach to make scientific claims is that the scientific community can collectively agree upon the severity with which a claim has been tested. If we design a study with 99.9% power for the smallest effect size of interest and use a 0.1% alpha level, everyone agrees the risk of an erroneous claim is low. If you personally do not like the claim, several options for criticism are possible. First, you can argue that no matter how small the error rate was, errors still  occur with their appropriate frequency, no matter how surprised we would be if they occur to us (I am paraphrasing Fisher). Thus, you might want to run two or three replications, until the probability of an error has become too small for the scientific community to consider it sensible to perform additional replication studies based on a cost-benefit analysis. Because it is practically very difficult to reach agreement on cost-benefit analyses, the field often resorts to rules or regulations. Just like we can debate if it is sensible to allow people to drive 138 kilometers per hour on some stretches of road at some time of the day if they have a certain level of driving experience, such discussions are currently too complex to practically implement, and instead, thresholds of 50, 80, 100, and 130  are used (depending on location and time of day). Similarly, scientific organizations decide upon thresholds that certain subfields are expected to use (such as an alpha level of 0.000003 in physics to declare a discovery, or the 2 study rule of the FDA).

 

Subjective Bayesian approaches can be used in practice to make scientific claims. For example, one can preregister that a claim will be made when a BF > 10 and smaller than 0.1. This is done in practice, for example in Registered Reports in Nature Human Behavior. The problem is that this methodological procedure does not in itself control the rate of erroneous claims. Some researchers have published frequentist analyses of Bayesian methodological decision rules (Note: Leonard Held brought up these Bayesian/Frequentist compromise methods as well – during coffee after our discussion, EJ and I agreed that we like those approaches, as they allow researcher to control frequentist errors, while interpreting the evidential value in the data – it is a win-won solution). This works by determining through simulations which test statistic should be used as a cut-off value to make claims. The process is often a bit laborious, but if you have the expertise and care about evidential interpretations of data, do it.

 

In practice, an advantage of frequentist approaches is that criticism has to focus on data and the experimental design, which can be resolved in additional experiments. In subjective Bayesian approaches, researchers can ignore the data and the experimental design, and instead waste time criticizing priors. For example, in a comment on Bem (2011) Wagenmakers and colleagues concluded that “We reanalyze Bem’s data with a default Bayesian t test and show that the evidence for psi is weak to nonexistent.” In a response, Bem, Utts, and Johnson stated “We argue that they have incorrectly selected an unrealistic prior distribution for their analysis and that a Bayesian analysis using a more reasonable distribution yields strong evidence in favor of the psi hypothesis.” I strongly expect that most reasonable people would agree more strongly with the prior chosen by Bem and colleagues, than the prior chosen by Wagenmakers and colleagues (Note: In the discussion EJ agreed he in hindsight did not believe the prior in the main paper was the best choice, but noted the supplementary files included a sensitivity analysis that demonstrated the conclusions were robust across a range of priors, and that the analysis by Bem et al combined Bayes factors in a flawed approach). More productively than discussing priors, data collected in direct replications since 2011 consistently lead to claims that there is no precognition effect. As Bem has not been able to succesfully counter the claims based on data collected in these replication studies, we can currently collectively as if Bem’s studies were all Type 1 errors (in part caused due to extensive p-hacking).

 

When do you think the other approach may be applicable?

 

Even when, in the approach the science I have described here, Bayesian approaches based on individual beliefs are not useful to make collectively agreed upon scientific claims, all scientists are Bayesians. First, we have to rely on our beliefs when we can not collect sufficient data to repeatedly test a prediction. When data is scarce, we can’t use a methodological procedure that makes claims with low error rates. Second, we can benefit from prior information when we know we can not be wrong. Incorrect priors can mislead, but if we know our priors are correct, even though this might be rare, use them. Finally, use individual beliefs when you are not interested in convincing others, but when you only want guide individual actions where being right or wrong does not impact others. For example, you can use your personal beliefs when you decide which study to run next.

 

Conclusion

 

In practice, analyses based on p-values and Bayes factors will often agree. Indeed, one of the points of discussion in the rest of the day was how we have bigger problems than the choice between statistical paradigms. A study with a flawed sample size justification or a bad measure is flawed, regardless of how we analyze the data. Yet, a good understanding of the value of the frequentist paradigm is important to be able to push back to problematic developments, such as researchers or journals who ignore the error rates of their claims, leading to rates of scientific claims that are incorrect too often. Furthermore, a discussion of this topic helps us think about whether we actually want to pursue the goals that our statistical tools achieve, and whether we actually want to organize knowledge generation by making scientific claims that others have to accept or criticize (a point we develop further in Uygun- Tunç, Tunç, & Lakens, https://psyarxiv.com/af9by/). Yes, discussions about P-Values and Bayes factors might in practice not have the biggest impact on improving our science, but it is still important and enjoyable to discuss these fundamental questions, and I’d like the thank EJ Wagenmakers and the audience for an extremely pleasant discussion.

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 effect 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 effects 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 effects 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 effects”. 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 effects 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).

Conclusion

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.

References

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