Andrew Gelman posted a link on his blog today to a paper by John Ioannidis I hadn’t seen before. In many respects, it’s basically the same paper I wrote earlier this year as a commentary on the Vul et al “voodoo correlations” paper (the commentary was itself based largely on an earlier chapter I wrote with my PhD advisor, Todd Braver). Well, except that the Ioannidis paper came out a year earlier than mine, and is also much better in just about every respect (more on this below).

What really surprises me is that I never came across Ioannidis’ paper when I was doing a lit search for my commentary. The basic point I made in the commentary–which can be summarized as the observation that low power coupled with selection bias almost invariably inflates significant effect sizes–is a pretty straightforward statistical point, so I figured that many people, and probably most statisticians, were well aware of it. But no amount of Google Scholar-ing helped me find an authoritative article that made the same point succinctly; I just kept coming across articles that made the point tangentially, in an off-hand “but of course we all know we shouldn’t trust these effect sizes, because…” kind of way. So I chalked it down as one of those statistical factoids (of which there are surprisingly many) that live in the unhappy land of too-obvious-for-statisticians-to-write-an-article-about-but-not-obvious-enough-for-most-psychologists-to-know-about. And so I just went ahead and wrote the commentary in a non-technical way that I hoped would get the point across intuitively.

Anyway, after the commentary was accepted, I sent a copy to Andrew Gelman, who had written several posts about the Vul et al controversy. He promptly send me back a link to this paper of his, which basically makes the same point about sampling error, but with much more detail and much better examples than I did. His paper also cites an earlier article in American Scientist by Wainer, which I also recommend, and again expresses very similar ideas. So then I felt a bit like a fool for not stumbling across either Gelman’s paper or Wainer’s earlier. And now that I’ve read Ioannidis’ paper, I feel even dumber, seeing as I could have saved myself a lot of trouble by writing two or three paragraphs and then essentially pointing to Ioannidis’ work. Oh well.

That all said, it wasn’t a complete loss; I still think the basic point is important enough that it’s worth repeating loudly and often, no matter how many times it’s been said before. And I’m skeptical that many fMRI researchers would have appreciated the point otherwise, given that none of the papers I’ve mentioned were published in venues fMRI researchers are likely to read regularly (which is presumably part of the reason I never came across them!). Of course, I don’t think that many people who do fMRI research actually bothered to read my commentary, so it’s questionable whether it had much impact anyway.

At any rate, the Ioannidis paper makes a number of points that my paper didn’t, so I figured I’d talk about them a bit. I’ll start by revisiting what I said in my commentary, and then I’ll tell you why you should read Ioannidis’ paper instead of mine.

The basic intuition can be captured as follows. Suppose you’re interested in the following question: Do clowns suffer depression at a higher rate than us non-comical folk do? You might think this is a contrived (to put it delicately) question, but I can assure you it has all sorts of important real-world implications. For instance, you wouldn’t be so quick to book a clown for your child’s next birthday party if you knew that The Great Mancini was going to be out in the parking lot half an hour later drinking cheap gin out of a top hat. If that example makes you feel guilty, congratulations: you’ve just discovered the translational value of basic science.

Anyway, back to the question, and how we’re going to answer it. You can’t just throw a bunch of clowns and non-clowns in a room and give them a depression measure. There’s nothing comical about that. What you need to do, if you’re rigorous about it, is give them *multiple* measures of depression, because we all know how finicky individual questionnaires can be. So the clowns and non-clowns each get to fill out the Beck Depression Inventory (BDI), the Center for Epidemiologic Studies Depression Scale, the Depression Adjective Checklist, the Zung Self-Rating Depression Scale (ZSRDS), and, let’s say, six other measures. Ten measures in all. And let’s say we have 20 individuals in each group, because that’s all I personally a cash-strapped but enthusiastic investigator can afford. After collecting the data, we score the questionnaires and run a bunch of t-tests to determine whether clowns and non-clowns have different levels of depression. Being scrupulous researchers who care a lot about multiple comparisons correction, we decide to divide our critical p-value by 10 (the dreaded Bonferroni correction, for 10 tests in this case) and test at p < .005. That’s a conservative analysis, of course; but better safe than sorry!

So we run our tests and get what look like mixed results. Meaning, we get statistically significant positive correlations between clown-dom status and depression for 2 measures–the BDI and Zung inventories–but not for the other 8 measures. So that’s admittedly not great; it would have been better if all 10 had come out right. Still, it at least partially supports our hypothesis: Clowns are fucking miserable! And because we’re already thinking ahead to how we’re going to present these results when they (inevitably) get published in Psychological Science, we go ahead and compute the effect sizes for the two significant correlations, because, after all, it’s important to know not only that there is a “real” effect, but also how big that effect is. When we do that, it turns out that the point-biserial correlation is huge! It’s .75 for the BDI and .68 for the ZSRDS. In other words, about half of the variance in clowndom can be explained by depression levels. And of course, because we’re well aware that correlation does not imply causation, we get to interpret the correlation both ways! So we quickly issue a press release claiming that we’ve discovered that it’s possible to conclusively diagnose depression just by knowing whether or not someone’s a clown! (We’re not going to worry about silly little things like base rates in a press release.)

Now, this may all seem great. And it’s probably not an unrealistic depiction of how much of psychology works (well, minus the colorful scarves, big hair, and face paint). That is, very often people report interesting findings that were selectively reported from amongst a larger pool of potential findings on the basis of the fact that the former but not the latter surpassed some predetermined criterion for statistical significance. For example, in our hypothetical in press clown paper, we don’t bother to report results for the correlation between clownhood and the Center for Epidemiologic Studies Depression Scale (r = .12, p > .1). Why should we? It’d be silly to report a whole pile of additional correlations only to turn around and say “null effect, null effect, null effect, null effect, null effect, null effect, null effect, and null effect” (see how boring it was to read that?). Nobody cares about variables that *don’t* predict other variables; we care about variables that *do* predict other variables. And we’re not really doing anything wrong, we think; it’s not like the act of selective reporting is inflating our Type I error (i.e., the false positive rate), because we’ve already taken care of that up front by deliberately being overconservative in our analyses.

Unfortunately, while it’s true that our Type I error doesn’t suffer, the act of choosing which findings to report based on the results of a statistical test does have another unwelcome consequence. Specifically, there’s a very good chance that the effect sizes we end up reporting for statistically significant results will be artificially inflated–perhaps dramatically so.

Why would this happen? It’s actually entailed by the selection procedure. To see this, let’s take the classical measurement model, under which the variance in any measured variable reflects the sum of two components: the “true” scores (i.e., the scores we would get if our measurements were always completely accurate) and some random error. The error term can in turn be broken down into many more specific sources of error; but we’ll ignore that and just focus on one source of error–namely, sampling error. Sampling error refers to the fact that we can never select a perfectly representative group of subjects when we collect a sample; there’s always some (ideally small) way in which the sample characteristics differ from the population. This error term can artificially inflate an effect or artificially deflate it, and it can inflate or deflate it more or less, but it’s going to have an effect one way or the other. You can take that to the bank as sure as my name’s Bozo the Clown.

To put this in context, let’s go back to our BDI scores. Recall that what we observed is that clowns have higher BDI scores than non-clowns. But what we’re now saying is that that difference in scores is going to be affected by sampling error. That is, just by chance, we may have selected a group of clowns that are particularly depressed, or a group of non-clowns who are particularly jolly. Maybe if we could measure depression in *all* clowns and *all *non-clowns, we would actually find no difference between groups.

Now, if we allow that sampling error really is random, and that we’re not actively trying to pre-determine the outcome of our study by going out of our way to recruit The Great Depressed Mancini and his extended dysthymic clown family, then in theory we have no reason to think that sampling error is going to introduce any particular bias into our results. It’s true that the observed correlations in our sample may not be perfectly representative of the true correlations in the population; but that’s not a big deal so long as there’s no systematic bias (i.e., that we have no reason to think that our sample will systematically inflate correlations or deflate them). But here’s the problem: *the act of choosing to report some correlations but not others on the basis of their statistical significance (or lack thereof) introduces precisely such a bias*. The reason is that, when you go looking for correlations that are of a certain size or greater, you’re inevitably going to be more likely to select those correlations that happen to have been helped by chance than hurt by it.

Here’s a series of figures that should make the point even clearer. Let’s pretend for a moment that the truth of the matter is that there is in fact a positive correlation between clown status and all 10 depression measures. Except, we’ll make it 100 measures, because it’ll be easier to illustrate the point that way. Moreover, let’s suppose that the correlation is exactly the same for all 100 measures, at .3. Here’s what that would look like if we just plotted the correlations for all 100 measures, 1 through 100:

It’s just a horizontal red line, because all the individual correlations have the same value (0.3). So that’s not very exciting. But remember, these are the *population* correlations. They’re not what we’re going to observe in our sample of 20 clowns and 20 non-clowns, because depression scores in our sample aren’t a perfect representation of the population. There’s also error to worry about. And error–or at least, sampling error–is going to be greater for smaller samples than for bigger ones. (The reason for this can be expressed intuitively: other things being equal, the more observations you have, the more representative your sample must be of the population as a whole, because deviations in any given direction will tend to cancel each other out the more data you collect. And if you keep collecting, at the limit, your sample will constitute the whole population, and must therefore by definition be perfectly representative). With only 20 subjects in each group, our estimates of each group’s depression level are not going to be terrifically stable. You can see this in the following figure, which shows the results of a simulation on 100 different variables, assuming that all have an identical underlying correlation of .3:

Notice how much variability there is in the correlations! The weakest correlation is actually negative, at -.18; the strongest is much larger than .3, at .63. (Caveat for more technical readers: this assumes that the above variables are completely independent, which in practice is unlikely to be true when dealing with 100 measures of the same construct.) So even though the *true* correlation is .3 in all cases, the magic of sampling will necessarily produce some values that are below .3, and some that are above .3. In some cases, the deviations will be substantial.

By now you can probably see where this is going. Here we have a distribution of effect sizes that to some extent may reflect underlying variability in population effect sizes, but is also almost certainly influenced by sampling error. And now we come along and decide that, hey, it doesn’t really make sense to report all 100 of these correlations in a paper; that’s too messy. Really, for the sake of brevity and clarity, we should only report those correlations that are in some sense more important and “real”. And we do that by calculating p-values and only reporting the results of tests that are significant at some predetermined level (in our case, p < .005). Well, here’s what that would look like:

This is exactly the same figure as the previous one, except we’ve now grayed out all the non-significant correlations. And in the process, we’ve made Bozo the Clown cry:

Why? Because unfortunately, the criterion that we’ve chosen is an extremely conservative one. In order to detect a significant difference in means between two groups of 20 subjects at p < .005, the observed correlation (depicted as the horizontal black line above) needs to be .42 or greater! That’s substantially larger than the actual population effect size of .3. Effects of this magnitude don’t occur very frequently in our sample; in fact, they only occur 16 times. As a result, we’re going to end up failing to detect 84 of 100 correlations, and will walk away thinking they’re null results–even though the truth is that, in the population, they’re actually *all* pretty strong, at .3. This quantity–the proportion of “real” effects that we’re likely to end up calling statistically significant given the constraints of our sample–is formally called statistical power. If you do a power analysis for a two-sample t-test on a correlation of .3 at p < .005, it turns out that power is only .17 (which is essentially what we see above; the slight discrepancy is due to chance). In other words, *even when there are real and relatively strong associations between depression and clownhood, our sample would only identify those associations 17% of the time, on average*.

That’s not good, obviously, but there’s more. Now the other shoe drops, because not only have we systematically missed out on most of the effects we’re interested in (in virtue of using small samples and overly conservative statistical thresholds), but notice what we’ve also done to the effect sizes of those correlations that we *do* end up identifying. What is in reality a .3 correlation spuriously appears, on average, asÂ a .51 correlation in the 16 tests that surpass our threshold. So, through the combined magic of low power and selection bias, we’ve turned what may in reality be a relatively diffuse association between two variables (say, clownhood and depression) into a seemingly selective and extremely strong association. After all the excitement about getting a high-profile publication, it might ultimately turn out that clowns aren’t really so depressed after all–it’s all an illusion induced by the sampling apparatus. So you might say that the clowns get the last laugh. Or that the joke’s on us. Or maybe just that this whole clown example is no longer funny and it’s now time for it to go bury itself in a hole somewhere.

Anyway, that, in a nutshell, was the point my commentary on the Vul et al paper made, and it’s the same point the Gelman and Wainer papers make too, in one way or another. While it’s a very general point that really applies in any domain where (a) power is less than 100% (which is just about always) and (b) there is some selection bias (which is also just about always), there were some considerations that were particularly applicable to fMRI research. The basic issue is that, in fMRI research, we often want to conduct analyses that span the entire brain, which means we’re usually faced with conducting many more statistical comparisons than researchers in other domains generally deal with (though not, say, molecular geneticists conducting genome-wide association studies). As a result, there is a very strong emphasis in imaging research on controlling Type I error rates by using very conservative statistical thresholds. You can agree or disagree with this general advice (for the record, I personally think there’s much too great an emphasis in imaging on Type I error, and not nearly enough emphasis on Type II error), but there’s no avoiding the fact that following it will tend to produce highly inflated significant effect sizes, because in the act of reducing p-value thresholds, we’re also driving down power dramatically, and making the selection bias more powerful.

While it’d be nice if there was an easy fix for this problem, there really isn’t one. In behavioral domains, there’s often a relatively simple prescription: report all effect sizes, both significant and non-significant. This doesn’t entirely solve the problem, because people are still likely to overemphasize statistically significant results relative to non-significant ones; but at least at that point you can say you’ve done what you can. In the fMRI literature, this course of action isn’t really available, because most journal editors are not going to be very happy with you when you send them a 25-page table that reports effect sizes and p-values for each of the 100,000 voxels you tested. So we’re forced adopt other strategies. The one I’ve argued for most strongly is to increase sample size (which increases power and decreases the uncertainty of resulting estimates). But that’s understandably difficult in a field where scanning each additional subject can cost $1,000 or more. There are a number of other things you can do, but I won’t talk about them much here, partly because this is already much too long a post, but mostly because I’m currently working on a paper that discusses this problem, and potential solutions, in much more detail.

So now finally I get to the Ioannidis article. As I said, the basic point is the same one made in my paper and Gelman’s and others, and the one I’ve described above in excruciating clownish detail. But there are a number of things about the Ioannidis that are particularly nice. One is that Ioannidis considers not only inflation due to selection of statistically significant results coupled with low power, but also inflation due to the use of flexible analyses (or, as he puts it, “vibration” of effects–also known as massaging the data). Another is that he considers cultural aspects of the phenomenon, e.g., the fact that investigators tend to be rewarded for reporting large effects, even if they subsequently fail to replicate. He also discusses conditions under which you might actually get deflation of effect sizes–something I didn’t touch on in my commentary, and hadn’t really thought about. Finally, he makes some interesting recommendations for minimizing effect size inflation. Whereas my commentary focused primarily on concrete steps researchers could take in individual studies to encourage clearer evaluation of results (e.g., reporting confidence intervals, including power calculations, etc.), Ioannidis focuses on longer-term solutions and the possibility that we’ll need to dramatically change the way we do science (at least in some fields).

Anyway, this whole issue of inflated effect sizes is a critical one to appreciate if you do any kind of social or biomedical science research, because it almost certainly affects your findings on a regular basis, and has all sorts of implications for what kind of research we conduct and how we interpret our findings. (To give just one trivial example, if you’ve ever been tempted to attribute your failure to replicate a previous finding to some minute experimental difference between studies, you should seriously consider the possibility that the original effect size may have been grossly inflated, and that your own study consequently has insufficient power to replicate the effect.) If you only have time to read one article that deals with this issue, read the Ioannidis paper. And remember it when you write your next Discussion section. Bozo the Clown will thank you for it.

Ioannidis, J. (2008). Why Most Discovered True Associations Are Inflated Epidemiology, 19 (5), 640-648 DOI: 10.1097/EDE.0b013e31818131e7

Yarkoni, T. (2009). Big Correlations in Little Studies: Inflated fMRI Correlations Reflect Low Statistical Power-Commentary on Vul et al. (2009) Perspectives on Psychological Science, 4 (3), 294-298 DOI: 10.1111/j.1745-6924.2009.01127.x

Hi Tal,

Great post. I agree this is a big issue in neuroscience research given the exploratory nature of the research and the small samples typically used.

A few random thoughts that I had:

1. If the journal does not have space to report all effect sizes, report the effect sizes available in an online supplement.

2. Distinguish exploratory from confirmatory analyses. Limit the confirmatory analyses to a small set. Then acknowledge the tentative and biased nature of the larger set of exploratory analyses.

3. Make the inferential approach for dealing with multiplicities in the data clear.

4. Consider the use of a big-picture to detailed approach. For example, if you are interested in the difference between clown and non-clown depression and you have multiple depression measures, take one measure to be the main test. This could be a composite of the measures used or perhaps the most reliable or valid measure.

In other contexts this might involve testing various alternative models of the relationship between a set of predictors and an outcome. One model could be an overall null hypothesis where all correlations are constrained to be zero. A second model could constrain all correlations to be equal, but non-zero. Additional models could test other particular patterns of interest. The fit of each model in absolute and relative terms could then be evaluated.

Don’t feel too bad – I’m an Ioannidis fan and I’d never heard of this paper before either!

The problem of effect size inflation is pretty easy to understand but as you say, solving it is hard. Still I wonder whether, in the case of fMRI specifically, there isn’t a possible solution…

“While itâ€™d be nice if there was an easy fix for this problem, there really isnâ€™t one. In behavioral domains, thereâ€™s often a relatively simple prescription: report all effect sizes, both significant and non-significant. This doesnâ€™t entirely solve the problem, because people are still likely to overemphasize statistically significant results relative to non-significant ones; but at least at that point you can say youâ€™ve done what you can. In the fMRI literature, this course of action isnâ€™t really available, because most journal editors are not going to be very happy with you when you send them a 25-page table that reports effect sizes and p-values for each of the 100,000 voxels you tested.”It’s true that no journal is going to publish all of the data from an fMRI experiment but – do we need journals to report fMRI results? Why couldn’t we make all of our results available online?

Suppose you look for a correlation between personality and neural activity in while looking at pictures of clowns. You take 10 personality measures and correlate each one with activity in every voxel. You apply a ridiculously conservative Bonferroni correction and you find some blobs where activity correlates very strongly with personality.

Now if you publish this in a journal, you’re only going to report those blobs where the effect size is very high. Because you will be applying a very conservative threshold. That’s the problem that Ioannidis and you identified. But what you actually have in this example is 10 3D brain volumes where higher values mean more correlation.

Why not make those 3D images your results, and leave it to the reader to threshold them? If the reader then wants to threshold them conservatively they can do so, knowing (hopefully) not to take the effect sizes too seriously, then if they want they can calculate the correlations in particular areas using different thresholds or no thresholds at all… all of which will be appropriate for certain purposes.

It’s always struck me as odd that we publish fMRI data in journals in exactly the same way as 19th century scientists published their results.

Hi Neuroskeptic,

Thanks for the comments and compliment!

Itâ€™s true that no journal is going to publish all of the data from an fMRI experiment but â€“ do we need journals to report fMRI results? Why couldnâ€™t we make all of our results available online?I totally agree with this idea, and it’s actually something I talk about as really being the ultimate long-term solution when I give talks on this stuff (and also in the paper I’m working on). Ultimately, the only (or at least, best) way to solve the problem is to dump all data, significant or not, in a massive database somewhere. But the emphasis in my post was on “easy” fixes, which this certainly isn’t. I think the main problem isn’t a technical one–there already are online databases (e.g., BrainMap and SuMS DB) that could in theory be modified to handle complete maps instead of coordinates–it’s a sociological one. It’s going to be pretty difficult to convince researchers to (a) allow their raw data to be submitted to a repository and (b) actually convince them to do it themselves (since it would inevitably entail filling out a bunch of meta-data for each map). I’m not saying this isn’t the way to go, just that it’s not going to be an easy sell.

The Journal of Cognitive Neuroscience already experimented with something like this back when they required authors to submit their raw data along with manuscripts. I think the general verdict is that it was a nice idea that didn’t really work in practice, because (a) it was a pain in the ass to process, (b) authors weren’t happy with it, and (c) hardly anyone actually requested or used the data. These aren’t insurmountable problems, and to some extent they’d be ameliorated by having an online database rather than an off-line one, but nonetheless, I think there are some big challenges involved…

Hi Tal,

That’s a nice write-up, but I’m wondering why you think there isn’t a practical “solution”? A whole-sale solution seems unlikely — publication bias will always be there in one form or another — but the huge exacerbation of this inflation that arises in fMRI (due to the sheer dimensionality of the data) can be solved:

Use one portion of the data to reduce the dimensionality to a much smaller set of ROIs, and the other part of the data to assess the effect size (either using independent localizers, or using cross-validation methods).

Using independent localizers to reduce the dimensionality of fMRI data (by several orders of magnitude) will go a long way to minimizing the problem: It will still be the case that the reported significant effects in any given ROI will be inflated, like all significant effects are inflated, but much less so. Moreover, if the dimensionality of fMRI is reduced sufficiently, there will only be a few ROIs, and reporting confidence intervals on non-significant effects ceases to be wildly impractical…

Cheers,

Ed

Hi Ed,

Thanks for the comment. I think cross-validation and independent localization are generally a good idea, but I’m not sure they help much with inflation caused by sampling error (as opposed to measurement error). Actually, there’s two issues. One is that power takes a hit any time you reduce the data. So in the case of individual differences in particular, I think it’s usually a bad idea to take a sample of, say, 20 subjects and split it in half, because (a) power in one half of the sample is going to be so low you won’t detect anything and (b) uncertainty in the other half is going to be so great you won’t be able to replicate anything anyway. But if you have a sample of, say, 500 people, and you’re not dealing with tiny effects, then sure, this is a good way to go (and is something I do when I have behavioral samples that big to work with).

Doing cross-validation or independent localization

withinsubjects is less of an issue from a power perspective. The problem here though is that you don’t necessarily reduce inflation that’s caused by sampling error. You can allow that you’re measuring each individual’s true score with perfect reliability and still have massive inflation caused by low power/selection bias. And cross-validation really won’t help you in that case. You could do even/odd runs or localizers or leave-one-out analyses, and the fundamental problem remains that people’s scores could be more or less the same across all permutations of the data and still grossly unrepresentative of the population distribution. That doesn’t mean we shouldn’t do these types of analyses, since they do nicely control for other types of error; but I’m not at all sure they do much to solve the particular problem I’m talking about.“The Journal of Cognitive Neuroscience already experimented with something like this back when they required authors to submit their raw data along with manuscripts.”Ah, I wasn’t aware of that. But that’s not quite what I was suggesting.

rawdata is not very interesting especially when it’s fMRI data which will take you at a minimum hours to analyze.I’d want the

finalanalyzed statistical parametric maps made available. And ideally all of the intermediate steps which the data went through on its journal from raw data to final results.My ultimate fantasy solution would be to have one massive supercomputer where everyone in the world uploads their data and does all their analysis, and everyone can see what everyone else is doing and everything they’ve ever done. This is not going to happen… but I think this is the ideal – total openness about what we do. Because frankly as scientists (and especially as scientists paid by the taxpayer!) we should be completely open about what we do, there shouldn’t be any “file drawers” at all.