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: https://mattiheino.com/2016/11/13/legacy-of-psychology/.

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.

Signed,

Daniel Lakens

Baguley, T. (2009). Standardized or simple effect size: What should be reported? British Journal of Psychology, 100(3), 603–617. https://doi.org/10.1348/000712608X377117

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. https://doi.org/10.1207/s15327957pspr0802_5

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. https://doi.org/10.3389/fpsyg.2013.00863

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. https://doi.org/10.1177/2515245918770963

Review of "The Generalizability Crisis" by Tal Yarkoni

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

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. https://doi.org/10.1073/pnas.1708285114

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). https://doi.org/10.1016/j.jml.2012.11.001

Box, G. E. (1976). Science and statistics. Journal of the American Statistical Association, 71(356), 791–799. https://doi.org/10/gdm28w

Clark, H. H. (1969). Linguistic processes in deductive reasoning. Psychological Review, 76(4), 387–404. https://doi.org/10.1037/h0027578

Cornfield, J., & Tukey, J. W. (1956). Average Values of Mean Squares in Factorials. The Annals of Mathematical Statistics, 27(4), 907–949. https://doi.org/10.1214/aoms/1177728067

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. https://doi.org/10.1007/s00221-009-1870-x

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. https://doi.org/10.31234/osf.io/jbh4w

Munafò, M. R., & Smith, G. D. (2018). Robust research needs many lines of evidence. Nature, 553(7689), 399–401. https://doi.org/10.1038/d41586-018-01023-3

Orben, A., & Lakens, D. (2019). Crud (Re)defined. https://doi.org/10.31234/osf.io/96dpy

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. https://doi.org/10.1177/1745691617708630

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 α% 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 (http://doi.org/10.1371/journal.pone.0127872). 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.


Code
For a related paper on alpha levels that in practical situations can not be 5%, see https://psyarxiv.com/erwvk/ 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 preregistering our 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 無 (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 will lead 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”.