Tag: replication

There is no ceiling effect in Johnson, Cheung, & Donnellan (2014)

This is not a blog post about bullying, negative psychology or replication studies in general. Those are important issues, and a lot of ink has been spilled over them in the past week or two. But this post isn’t about those issues (at least, not directly). This post is about ceiling effects. Specifically, the ceiling effect purportedly present in a paper in Social Psychology, in which Johnson, Cheung, and Donnellan report the results of two experiments that failed to replicate an earlier pair of experiments by Schnall, Benton, and Harvey.

If you’re not up to date on recent events, I recommend reading Vasudevan Mukunth’s post, which provides a nice summary. If you still want to know more after that, you should probably take a gander at the original paper by Schnall, Benton, & Harvey and the replication paper. Still want more? Go read Schnall’s rebuttal. Then read the rejoinder to the rebuttal. Then read Schnall’s first and second blog posts. And maybe a number of other blog posts (here, here, here, and here). Oh, and then, if you still haven’t had enough, you might want to skim the collected email communications between most of the parties in question, which Brian Nosek has been kind enough to curate.

I’m pointing you to all those other sources primarily so that I don’t have to wade very deeply into the overarching issues myself–because (a) they’re complicated, (b) they’re delicate, and (c) I’m still not entirely sure exactly how I feel about them. However, I do have a fairly well-formed opinion about the substantive issue at the center of Schnall’s published rebuttal–namely, the purported ceiling effect that invalidates Johnson et al’s conclusions. So I thought I’d lay that out here in excruciating detail. I’ll warn you right now that if your interests lie somewhere other than the intersection of psychology and statistics (which they probably should), you probably won’t enjoy this post very much. (If your interests do lie at the intersection of psychology and statistics, you’ll probably give this post a solid “meh”.)

Okay, with all the self-handicapping out of the way, let’s get to it. Here’s what I take to be…

Schnall’s argument

The crux of Schnall’s criticism of the Johnson et al replication is a purported ceiling effect. What, you ask, is a ceiling effect? Here’s Schnall’s definition:

A ceiling effect means that responses on a scale are truncated toward the top end of the scale. For example, if the scale had a range from 1-7, but most people selected “7”, this suggests that they might have given a higher response (e.g., “8” or “9”) had the scale allowed them to do so. Importantly, a ceiling effect compromises the ability to detect the hypothesized influence of an experimental manipulation. Simply put: With a ceiling effect it will look like the manipulation has no effect, when in reality it was unable to test for such an effects in the first place. When a ceiling effect is present no conclusions can be drawn regarding possible group differences.

This definition has some subtle-but-important problems we’ll come back to, but it’s reasonable as a first approximation. With this definition in mind, here’s how Schnall describes her core analysis, which she uses to argue that Johnson et al’s results are invalid:

Because a ceiling effect on a dependent variable can wash out potential effects of an independent variable (Hessling, Traxel & Schmidt, 2004), the relationship between the percentage of extreme responses and the effect of the cleanliness manipulation was examined. First, using all 24 item means from original and replication studies, the effect of the manipulation on each item was quantified. … Second, for each dilemma the percentage of extreme responses averaged across neutral and clean conditions was computed. This takes into account the extremity of both conditions, and therefore provides an unbiased indicator of ceiling per dilemma. … Ceiling for each dilemma was then plotted relative to the effect of the cleanliness manipulation (Figure 1).

We can (and will) quibble with these analysis choices, but the net result of the analysis is this:

schnall_figure

Here, we see normalized effect size (y-axis) plotted against extremity of item response (x-axis). Schnall’s basic argument is that there’s a strong inverse relationship between the extremity of responses to an item and the size of the experimental effect on that item. In other words, items with extreme responses don’t show an effect, whereas items with non-extreme responses do show an effect. She goes on to note that this pattern is full accounted for by her own original experiments, and that there is no such relationship in Johnson et al’s data. On the basis of this finding, Schnall concludes that:

Scores are compressed toward the top end of the scale and therefore show limited determinate variance near ceiling. Because a significance test compares variance due to a manipulation to variance due to error, an observed lack of effect can result merely from a lack in variance that would normally be associated with a manipulation. Given the observed ceiling effect, a statistical artefact, the analyses reported by Johnson et al. (2014a) are invalid and allow no conclusions about the reproducibility of the original findings.

Problems with the argument

One can certainly debate over what the implications would be even if Schnall’s argument were correct; for instance, it’s debatable whether the presence of a ceiling effect would actually invalidate Johnson et al’s conclusions that they had failed to replicate Schnall et al. An alternative and reasonable interpretation is that Johnson et al would have simply identified important boundary conditions under which the original effect doesn’t work (e.g., that it doesn’t hold in Michigan residents), since they were using Schnall’s original measures. But we don’t have to worry about that in any case, because there are several serious problems with Schnall’s argument. Some of them have to do with the statistical analysis she performs to make her point; some of them have to do with subtle mischaracterizations of what ceiling effects are and where they come from; and some of them have to do with the fact that Schnall’s data actually directly contradict her own argument. Let’s take each of these in turn.

Problems with the analysis

A first problem with Schnall’s analysis is that the normalization procedure she uses to make her point is biased. Schnall computes the normalized effect size for each item as:

(M1 – M2)/(M1 + M2)

Where M1 and M2 are the means for each item in the two experimental conditions (neutral and clean). This transformation is supposed to account for the fact that scores are compressed at the upper end of the scale, near the ceiling.

What Schnall fails to note, however, is that compression should also occur at the bottom of the scale, near the floor. For example, suppose an individual item has means of 1.2 and 1.4. Then Schnall’s normalized effect size estimate would be 0.2/2.6 = 0.07. But if the means had been 4.0 and 4.2–the same relative difference–then the adjusted estimate would actually be much smaller (around 0.02). So Schnall’s analysis is actually biased in favor of detecting the negative correlation she takes as evidence of a ceiling effect, because she’s not accounting for floor effects simultaneously. A true “clipping” or compression of scores shouldn’t occur at only one extreme of the scale; what should matter is how far from the midpoint a response happens to be. What should happen, if Schnall were to recompute the scores in Figure 1 using a modified criterion (e.g., relative deviation from the scale’s midpoint, rather than absolute score), is that the points at the top left of the figure should pull towards the y-axis to some degree, effectively reducing the slope she takes as evidence of a problem. If there’s any pattern that would suggest a measurement problem, it’s actually an inverted u-shape, where normalized effects are greatest for items with means nearest the midpoint, and smallest for items at both extremes, not just near ceiling. But that’s not what we’re shown.

A second problem is that Schnall’s data actually contradict her own conclusion. She writes:

Across the 24 dilemmas from all 4 experiments, dilemmas with a greater percentage of extreme responses were associated with lower effect sizes (r = -.50, p = .01, two-tailed). This negative correlation was entirely driven by the 12 original items, indicating that the closer responses were to ceiling, the smaller was the effect of the manipulation (r = -.49, p = .10).4In contrast, across the 12 replication items there was no correlation (r = .11, p = .74).

But if anything, these results provide evidence of a ceiling effect only in Schnall’s original study, and not in the Johnson et al replications. Recall that Schnall’s argument rests on two claims: (a) effects are harder to detect the more extreme responding on an item gets, and (b) responding is so extreme on the items in the Johnson et al experiments that nothing can be detected. But the results she presents blatantly contradict the second claim. Had there been no variability in item means in the Johnson et al studies, Schnall could have perhaps argued that restriction of range is so extreme that it is impossible to detect any kind of effect. In practice, however, that’s not the case. There is considerable variability along the x-axis, and in particular, one can clearly see that there are two items in Johnson et al that are nowhere near ceiling and yet show no discernible normalized effect of experimental condition at all. Note that these are the very same items that show some of the strongest effects in Schnall’s original study. In other words, the data Schnall presents in support of her argument actually directly contradict her argument. If one is to believe that a ceiling effect is preventing Schnall’s effect from emerging in Johnson et al’s replication studies, then there is no reasonable explanation for the fact that those two leftmost red squares in the figure above are close to the y = 0 line. They should be behaving exactly like they did in Schnall’s study–which is to say, they should be showing very large normalized effects–even if items at the very far right show no effects at all.

Third, Schnall’s argument that a ceiling effect completely invalidates Johnson et al’s conclusions is a gross exaggeration. Ceiling effects are not all-or-none; the degree of score compression into the upper end of a measure will vary continuously (unless there is literally no variance at all in the reponses, which is clearly not the case here). Even if we took at face value Schnall’s finding that there’s an inverse relationship between effect size and extremity in her original data (r = -0.5), all this would tell us is that there’s some compression of scores. Schnall’s suggestion that “given the observed ceiling effect, a statistical artifact, the analyses reported in Johnson et al (2014a) are invalid and allow no conclusions about the reproducibility of the original findings” is simply false. Even in the very best case scenario (which this obviously isn’t), the very strongest claim Schnall could comfortably make is that there may be some compression of scores, with unknown impact on the detectable effect size. It is simply not credible for Schnall to suggest that the mere presence of something that looks vaguely like a ceiling effect is sufficient to completely rule out detection of group differences in the Johnson et al experiments. And we know this with 100% certainty, because…

There are robust group differences in the replication experiments

Perhaps the clearest refutation of Schnall’s argument for a ceiling effect is that, as Johnson et al noted in their rejoinder, the Johnson et al experiments did in fact successfully identify some very clear group differences (and, ironically, ones that were also present in Schnall’s original experiments). Specifically, Johnson et al showed a robust effect of gender on vignette ratings. Here’s what the results look like:

We can see clearly that, in both replication experiments, there’s a large effect of gender but no discernible effect of experimental condition. This pattern directly refutes Schnall’s argument. She cannot have it both ways: if a ceiling effect precludes the presence of group differences, then there cannot be a ceiling effect in the replication studies, or else the gender effect could not have emerged repeatedly. Conversely, if ceiling effects don’t preclude detection of effects, then there is no principled reason why Johnson et al would fail to detect Schnall’s original effect.

Interestingly, it’s not just the overall means that tell the story quite clearly. Here’s what happens if we plot the gender effects in Johnson et al’s experiments in the same way as Schnall’s Figure 1 above:

gender_fx_by_extremity

Notice that we see here the same negative relationship between effect size and extremity that Schnall observed in her own data, and whose absence in Johnson et al’s data she (erroneously) took as evidence of a ceiling effect.

There’s a ceiling effect in Schnall’s own data

Yet another flaw in Schnall’s argument is that taking the ceiling effect charge seriously would actually invalidate at least one of her own experiments. Consider that the only vignette in Schnall et al’s original Experiment 1 that showed a statistically significant effect also had the highest rate of extreme responding in that study (mean rating of 8.25 / 9). Even more strikingly, the proportion of participants who gave the most extreme response possible on that vignette (70%) was higher than for any of the vignettes in either of Johnson et al’s experiments. In other words, Schnall’s core argument is that her effect could not possibly be replicated in Johnson et al’s experiments because of the presence of a ceiling effect, yet the only vignette to show a significant effect in Schnall’s original Experiment 1 had an even more pronounced ceiling effect. Once again, she cannot have it both ways. Either ceiling effects don’t preclude detection of effects, or, by Schnall’s own logic, the original Study 1 effect was probably a false positive.

When pressed on this point by Daniel Lakens in the email thread, Schnall gave the following response:

Note for the original studies we reported that the effect was seen on aggregate data, not necessarily for individual dilemmas. Such results will always show statistical fluctuations at the item level, hence it is important to not focus on any individual dilemma but on the overall pattern.

I confess that I’m not entirely clear on what Schnall means here. One way to read this is that she is conceding that the significant effect in the vignette in question (the “kitten” dilemma) was simply due to random fluctuations. Note that since the effect in Schnall’s Experiment 1 was only barely significant when averaging across all vignettes (in fact, it wasn’t quite significant even so), eliminating this vignette from consideration would actually have produced a null result. But suppose we overlook that and instead agree with Schnall that strange things can happen to individual items, and that what we should focus on is the aggregate moral judgment, averaged across vignettes. That would be perfectly reasonable, except that it’s directly at odds with Schnall’s more general argument. To see this, we need only look at the aggregate distribution of scores in Johnson et al’s Experiments 1 and 2:

johnson_distributions

There’s clearly no ceiling effect here; the mode in both experiments is nowhere near the maximum. So once again, Schnall can’t have it both ways. If her argument is that what matters is the aggregate measure (which seems right to me, since many reputable measures have multiple individual items with skewed distributions, and this can even be a desirable property in certain cases), then there’s nothing objectionable about the scores in the Johnson et al experiments. Conversely, if Schnall’s argument is that it’s fair to pick on individual items, then there is effectively no reason to believe Schnall’s own original Experiment 1 (and for all I know, her experiment 2 as well–I haven’t looked).

What should we conclude?

What can we conclude from all this? A couple of things. First, Schnall has no basis for arguing that there was a fundamental statistical flaw that completely invalidates Johnson et al’s conclusions. From where I’m sitting, there doesn’t seem to be any meaningful ceiling effect in Johnson et al’s data, and that’s attested to by the fact that Johnson et al had no trouble detecting gender differences in both experiments (successfully replicating Schnall’s earlier findings). Moreover, the arguments Schnall makes in support of the postulated ceiling effects suffer from serious flaws. At best, what Schnall could reasonably argue is that there might be some restriction of range in the ratings, which would artificially reduce the effect size. However, given that Johnson et al’s sample sizes were 3 – 5 times larger than Schnall’s, it is highly implausible to suppose that effects as big as Schnall’s completely disappeared–especially given that robust gender effects were detected. Moreover, given that the skew in Johnson et al’s aggregate distributions is not very extreme at all, and that many individual items on many questionnaire measures show ceiling or floor effects (e.g., go look at individual Big Five item distributions some time), taking Schnall’s claims seriously one would in effect invalidate not just Johnson et al’s results, but also a huge proportion of the more general psychology literature.

Second, while Schnall has raised a number of legitimate and serious concerns about the tone of the debate and comments surrounding Johnson et al’s replication, she’s also made a number of serious charges of her own that depend on the validity of her argument about celing effects, and not on the civility (or lack thereof) of commentators on various sides of the debate. Schnall has (incorrectly) argued that Johnson et al have committed a basic statistical error that most peer reviewers would have caught–effectively accusing them of incompetence. She has argued that Johnson et al’s claim of replication failure is unwarranted, and constitutes defamation of her scientific reputation. And she has suggested that the editors of the special issue (Daniel Lakens and Brian Nosek) behaved unethically by first not seeking independent peer review of the replication paper, and then actively trying to suppress her own penetrating criticisms. In my view, none of these accusations are warranted, because they depend largely on Schnall’s presumption of a critical flaw in Johnson et al’s work that is in fact nonexistent. I understand that Schnall has been under a lot of stress recently, and I sympathize with her concerns over unfair comments made by various people (most of whom have now issued formal apologies). But given the acrimonious tone of the more general ongoing debate over replication, it’s essential that we distinguish the legitimate issues from the illegitimate ones so that we can focus exclusively on the former, and don’t end up needlessly generating more hostility on both sides.

Lastly, there is the question of what conclusions we should draw from the Johnson et al replication studies. Personally, I see no reason to question Johnson et al’s conclusions, which are actually very modest:

In short, the current results suggest that the underlying effect size estimates from these replication experiments are substantially smaller than the estimates generated from the original SBH studies. One possibility is that there are unknown moderators that account for these apparent discrepancies. Perhaps the most salient difference betweenthe current studies and the original SBH studies is the student population. Our participants were undergraduates inUnited States whereas participants in SBH’sstudies were undergraduates in the United Kingdom. It is possible that cultural differences in moral judgments or in the meaning and importance of cleanliness may explain any differences.

Note that Johnson et al did not assert or intimate in any way that Schnall et al’s effects were “not real”. They did not suggest that Schnall et al had committed any errors in their original study. They explicitly acknowledged that unknown moderators might explain the difference in results (though they also noted that this was unlikely considering the magnitude of the differences). Effectively, Johnson et al stuck very close to their data and refrained from any kind of unfounded speculation.

In sum, unless Schnall has other concerns about Johnson’s data besides the purported ceiling effect (and she hasn’t raised any that I’ve seen), I think Johnson et al’s paper should enter the record exactly as its authors intended. Johnson, Cheung, & Donnellan (2014) is, quite simply, a direct preregistered replication of Schnall, Benton, & Harvey (2008) that failed to detect the effects reported in the original study, and there should be nothing at all controversial about this. There are certainly worthwhile discussions to be had about why the replication failed, and what that means for the original effect, but this doesn’t change the fundamental fact that the replication did fail, and we shouldn’t pretend otherwise.

What we can and can’t learn from the Many Labs Replication Project

By now you will most likely have heard about the “Many Labs” Replication Project (MLRP)–a 36-site, 12-country, 6,344-subject effort to try to replicate a variety of classical and not-so-classical findings in psychology. You probably already know that the authors tested a variety of different effects–some recent, some not so recent (the oldest one dates back to 1941!); some well-replicated, others not so much–and reported successful replications of 10 out of 13 effects (though with widely varying effect sizes).

By and large, the reception of the MLRP paper has been overwhelmingly positive. Setting aside for the moment what the findings actually mean (see also Rolf Zwaan’s earlier take), my sense is that most psychologists are united in agreement that the mere fact that researchers at 36 different sites were able to get together and run a common protocol testing 13 different effects is a pretty big deal, and bodes well for the field in light of recent concerns about iffy results and questionable research practices.

But not everyone’s convinced. There now seems to be something of an incipient backlash against replication. Or perhaps not so much against replication itself as against the notion that the ongoing replication efforts have any special significance. An in press paper by Joseph Cesario makes a case for deferring independent efforts to replicate an effect until the original effect is theoretically well understood (a suggestion I disagree with quite strongly, and plan to follow up on in a separate post). And a number of people have questioned, in blog comments and tweets, what the big deal is. A case in point:

I think the charitable way to interpret this sentiment is that Gilbert and others are concerned that some people might read too much into the fact that the MLRP successfully replicated 10 out of 13 effects. And clearly, at least some journalists have; for instance, Science News rather irresponsibly reported that the MLRP “offers reassurance” to psychologists. That said, I don’t think it’s fair to characterize this as anything close to a dominant reaction, and I don’t think I’ve seen any researchers react to the MLRP findings as if the 10/13 number means anything special. The piece Dan Gilbert linked to in his tweet, far from promoting “hysteria” about replication, is a Nature News article by the inimitable Ed Yong, and is characteristically careful and balanced. Far from trumpeting the fact that 10 out of 13 findings replicated, here’s a direct quote from the article:

Project co-leader Brian Nosek, a psychologist at the Center of Open Science in Charlottesville, Virginia, finds the outcomes encouraging. “It demonstrates that there are important effects in our field that are replicable, and consistently so,“ he says. “But that doesn’t mean that 10 out of every 13 effects will replicate.“

Kahneman agrees. The study “appears to be extremely well done and entirely convincing“, he says, “although it is surely too early to draw extreme conclusions about entire fields of research from this single effort“.

Clearly, the mere fact that 10 out of 13 effects replicated is not in and of itself very interesting. For one thing (and as Ed Yong also noted in his article), a number of the effects were selected for inclusion in the project precisely because they had already been repeatedly replicated. Had the MLRP failed to replicate these effects–including, for instance, the seminal anchoring effect discovered by Kahneman and Tversky in the 1970s–the conclusion would likely have been that something was wrong with the methodology, and not that the anchoring effect doesn’t exist. So I think pretty much everyone can agree with Gilbert that we have most assuredly not learned, as a result of the MLRP, that there’s no replication crisis in psychology after all, and that roughly 76.9% of effects are replicable. Strictly speaking, all we know is that there are at least 10 effects in all of psychology that can be replicated. But that’s not exactly what one would call an earth-shaking revelation. What’s important to appreciate, however, is that the utility of the MLRP was never supposed to be about the number of successfully replicated effects. Rather, its value is tied to a number of other findings and demonstrations–some of which are very important, and have potentially big implications for the field at large. To wit:

1. The variance between effects is greater than the variance within effects.

Here’s the primary figure from the MLRP paper: Many Labs Replication Project results

Notice that the range of meta-analytic estimates for the different effect sizes (i.e., the solid green circles) is considerably larger than the range of individual estimates within a given effect. In other words, if you want to know how big a given estimate is likely to be, it’s more informative to know what effect is being studied than to know which of the 36 sites is doing the study. This may seem like a rather esoteric point, but it has important implications. Most notably, it speaks directly to the question of how much one should expect effect sizes to fluctuate from lab to lab when direct replications are attempted. If you’ve been following the controversy over the relative (non-)replicability of a number of high-profile social priming studies, you’ve probably noticed that a common defense researchers use when their findings fails to replicate is to claim that the underlying effect is very fragile, and can’t be expected to work in other researchers’ hands. What the MLRP shows, for a reasonable set of studies, is that there does not in fact appear to be a huge amount of site-to-site variability in effects. Take currency priming, for example–an effect in which priming participants with money supposedly leads them to express capitalistic beliefs and behaviors more strongly. Given a single failure to replicate the effect, one could plausibly argue that perhaps the effect was simply too fragile to reproduce consistently. But when 36 different sites all produce effects within a very narrow range–with a mean that is effectively zero–it becomes much harder to argue that the problem is that the effect is highly variable. To the contrary, the effect size estimates are remarkably consistent–it’s just that they’re consistently close to zero.

2. Larger effects show systematically greater variability.

You can see in the above figure that the larger an effect is, the more individual estimates appear to vary across sites. In one sense, this is not terribly surprising–you might already have the statistical intuition that the larger an effect is, the more reliable variance should be available to interact with other moderating variables. Conversely, if an effect is very small to begin with, it’s probably less likely that it could turn into a very large effect under certain circumstances–or that it might reverse direction entirely. But in another sense, this finding is actually quite unexpected, because, as noted above, there’s a general sense in the field that it’s the smaller effects that tend to be more fragile and heterogeneous. To the extent we can generalize from these 13 studies, these findings should give researchers some pause before attributing replication failures to invisible moderators that somehow manage to turn very robust effects (e.g., the original currency priming effect was nearly a full standard deviation in size) into nonexistent ones.

3. A number of seemingly important variables don’t systematically moderate effects.

There have long been expressions of concern over the potential impact of cultural and population differences on psychological effects. For instance, despite repeated demonstrations that internet samples typically provide data that are as good as conventional lab samples, many researchers continue to display a deep (and in my view, completely unwarranted) skepticism of findings obtained online. More reasonably, many researchers have worried that effects obtained using university students in Western nations–the so-called WEIRD samples–may not generalize to other social groups, cultures and countries. While the MLRP results are obviously not the last word on this debate, it’s instructive to note that factors like data acquisition approach (online vs. offline) and cultural background (US vs. non-US) didn’t appear to exert a systematic effect on results. This doesn’t mean that there are no culture-specific effects in psychology of course (there undoubtedly are), but simply that our default expectation should probably be that most basic effects will generalize across cultures to at least some extent.

4. Researchers have pretty good intuitions about which findings will replicate and which ones won’t.

At the risk of offending some researchers, I submit that the likelihood that a published finding will successfully replicate is correlated to some extent with (a) the field of study it falls under and (b) the journal in which it was originally published. For example, I don’t think it’s crazy to suggest that if one were to try to replicate all of the social priming studies and all of the vision studies published in Psychological Science in the last decade, the vision studies would replicate at a consistently higher rate. Anecdotal support for this intuition comes from a string of high-profile failures to replicate famous findings–e.g., John Bargh’s demonstration that priming participants with elderly concepts leads them to walk away from an experiment more slowly. However, the MLRP goes one better than anecdote, as it included a range of effects that clearly differ in their a priori plausibility. Fortuitously, just prior to publicly releasing the MLRP results, Brian Nosek asked the following question on Twitter:

Several researchers, including me, took Brian up on his offers; here are the responses:

As you can see, pretty much everyone that replied to Brian expressed skepticism about the two priming studies (#9 and #10 in Hal Pashler’s reply). There was less consensus on the third effect. (Actually, as it happens, there were actually ultimately only 2 failures to replicate–the third effect became statistically significant when samples were weighted properly.) Nonetheless, most of us picked Imagined Contact as number 3, which did in fact emerge as the smallest of the statistically significant effects. (It’s probably worth mentioning that I’d personally only heard of 4 or 5 of the 13 effects prior to reading their descriptions, so it’s not as though my response was based on a deep knowledge of prior work on these effects–I simply read the descriptions of the findings and gauged their plausibility accordingly.)

Admittedly, these are just two (or three) studies. It’s possible that the MLRP researchers just happened to pick two of the only high-profile priming studies that both seem highly counterintuitive and happen to be false positives. That said, I don’t really think these findings stand out from the mass of other counterintuitive priming studies in social psychology in any way. While we obviously shouldn’t conclude from this that no high-profile, counterintuitive priming studies will successfully replicate, the fact that a number of researchers were able to prospectively determine, with a high degree of accuracy, which effects would fail to replicate (and, among those that replicated, which were rather weak), is a pretty good sign that researchers’ intuitions about plausibility and replicability are pretty decent.

Personally, I’d love to see this principle pushed further, and formalized as a much broader tool for evaluating research findings. For example, one can imagine a website where researchers could publicly (and perhaps anonymously) register their degree of confidence in the likely replicability of any finding associated with a doi or PubMed ID. I think such a service would be hugely valuable–not only because it would help calibrate individual researchers’ intuitions and provide a sense of the field’s overall belief in an effect, but because it would provide a useful index of a finding’s importance in the event of successful replication (i.e., the authors of a well-replicated finding should probably receive more credit if the finding was initially viewed with great skepticism than if it was universally deemed rather obvious).

There are other potentially important findings in the MLRP paper that I haven’t mentioned here (see Rolf Zwaan’s blog post for additional points), but if nothing else, I hope this will help convince any remaining skeptics that this is indeed a landmark paper for psychology–even though the number of successful replications is itself largely meaningless.

Oh, there’s one last point worth mentioning, in light of the rather disagreeable tone of the debate surrounding previous replication efforts. If your findings are ever called into question by a multinational consortium of 36 research groups, this is exactly how you should respond:

Social psychologist Travis Carter of Colby College in Waterville, Maine, who led the original flag-priming study, says that he is disappointed but trusts Nosek’s team wholeheartedly, although he wants to review their data before commenting further. Behavioural scientist Eugene Caruso at the University of Chicago in Illinois, who led the original currency-priming study, says, “We should use this lack of replication to update our beliefs about the reliability and generalizability of this effect“, given the “vastly larger and more diverse sample“ of the MLRP. Both researchers praised the initiative.

Carter and Caruso’s attitude towards the MLRP is really exemplary; people make mistakes all the time when doing research, and shouldn’t be held responsible for the mere act of publishing incorrect findings (excepting cases of deliberate misconduct or clear negligence). What matters is, as Caruso notes, whether and to what extent one shows a willingness to update one’s beliefs in response to countervailing evidence. That’s one mark of a good scientist.

the truth is not optional: five bad reasons (and one mediocre one) for defending the status quo

You could be forgiven for thinking that academic psychologists have all suddenly turned into professional whistleblowers. Everywhere you look, interesting new papers are cropping up purporting to describe this or that common-yet-shady methodological practice, and telling us what we can collectively do to solve the problem and improve the quality of the published literature. In just the last year or so, Uri Simonsohn introduced new techniques for detecting fraud, and used those tools to identify at least 3 cases of high-profile, unabashed data forgery. Simmons and colleagues reported simulations demonstrating that standard exploitation of research degrees of freedom in analysis can produce extremely high rates of false positive findings. Pashler and colleagues developed a “Psych file drawer” repository for tracking replication attempts. Several researchers raised trenchant questions about the veracity and/or magnitude of many high-profile psychological findings such as John Bargh’s famous social priming effects. Wicherts and colleagues showed that authors of psychology articles who are less willing to share their data upon request are more likely to make basic statistical errors in their papers. And so on and so forth. The flood shows no signs of abating; just last week, the APS journal Perspectives in Psychological Science announced that it’s introducing a new “Registered Replication Report” section that will commit to publishing pre-registered high-quality replication attempts, irrespective of their outcome.

Personally, I think these are all very welcome developments for psychological science. They’re solid indications that we psychologists are going to be able to police ourselves successfully in the face of some pretty serious problems, and they bode well for the long-term health of our discipline. My sense is that the majority of other researchers–perhaps the vast majority–share this sentiment. Still, as with any zeitgeist shift, there are always naysayers. In discussing these various developments and initiatives with other people, I’ve found myself arguing, with somewhat surprising frequency, with people who for various reasons think it’s not such a good thing that Uri Simonsohn is trying to catch fraudsters, or that social priming findings are being questioned, or that the consequences of flexible analyses are being exposed. Since many of the arguments I’ve come across tend to recur, I thought I’d summarize the most common ones here–along with the rebuttals I usually offer for why, with one possible exception, the arguments for giving a pass to sloppy-but-common methodological practices are not very compelling.

“But everyone does it, so how bad can it be?”

We typically assume that long-standing conventions must exist for some good reason, so when someone raises doubts about some widespread practice, it’s quite natural to question the person raising the doubts rather than the practice itself. Could it really, truly be (we say) that there’s something deeply strange and misguided about using p values? Is it really possible that the reporting practices converged on by thousands of researchers in tens of thousands of neuroimaging articles might leave something to be desired? Could failing to correct for the many researcher degrees of freedom associated with most datasets really inflate the false positive rate so dramatically?

The answer to all these questions, of course, is yes–or at least, we should allow that it could be yes. It is, in principle, entirely possible for an entire scientific field to regularly do things in a way that isn’t very good. There are domains where appeals to convention or consensus make perfect sense, because there are few good reasons to do things a certain way except inasmuch as other people do them the same way. If everyone else in your country drives on the right side of the road, you may want to consider driving on the right side of the road too. But science is not one of those domains. In science, there is no intrinsic benefit to doing things just for the sake of convention. In fact, almost by definition, major scientific advances are ones that tend to buck convention and suggest things that other researchers may not have considered possible or likely.

In the context of common methodological practice, it’s no defense at all to say but everyone does it this way, because there are usually relatively objective standards by which we can gauge the quality of our methods, and it’s readily apparent that there are many cases where the consensus approach leave something to be desired. For instance, you can’t really justify failing to correct for multiple comparisons when you report a single test that’s just barely significant at p < .05 on the grounds that nobody else corrects for multiple comparisons in your field. That may be a valid explanation for why your paper successfully got published (i.e., reviewers didn’t want to hold your feet to the fire for something they themselves are guilty of in their own work), but it’s not a valid defense of the actual science. If you run a t-test on randomly generated data 20 times, you will, on average, get a significant result, p < .05, once. It does no one any good to argue that because the convention in a field is to allow multiple testing–or to ignore statistical power, or to report only p values and not effect sizes, or to omit mention of conditions that didn’t ‘work’, and so on–it’s okay to ignore the issue. There’s a perfectly reasonable question as to whether it’s a smart career move to start imposing methodological rigor on your work unilaterally (see below), but there’s no question that the mere presence of consensus or convention surrounding a methodological practice does not make that practice okay from a scientific standpoint.

“But psychology would break if we could only report results that were truly predicted a priori!”

This is a defense that has some plausibility at first blush. It’s certainly true that if you force researchers to correct for multiple comparisons properly, and report the many analyses they actually conducted–and not just those that “worked”–a lot of stuff that used to get through the filter will now get caught in the net. So, by definition, it would be harder to detect unexpected effects in one’s data–even when those unexpected effects are, in some sense, ‘real’. But the important thing to keep in mind is that raising the bar for what constitutes a believable finding doesn’t actually prevent researchers from discovering unexpected new effects; all it means is that it becomes harder to report post-hoc results as pre-hoc results. It’s not at all clear why forcing researchers to put in more effort validating their own unexpected finding is a bad thing.

In fact, forcing researchers to go the extra mile in this way would have one exceedingly important benefit for the field as a whole: it would shift the onus of determining whether an unexpected result is plausible enough to warrant pursuing away from the community as a whole, and towards the individual researcher who discovered the result in the first place. As it stands right now, if I discover an unexpected result (p < .05!) that I can make up a compelling story for, there’s a reasonable chance I might be able to get that single result into a short paper in, say, Psychological Science. And reap all the benefits that attend getting a paper into a “high-impact” journal. So in practice there’s very little penalty to publishing questionable results, even if I myself am not entirely (or even mostly) convinced that those results are reliable. This state of affairs is, to put it mildly, not A Good Thing.

In contrast, if you as an editor or reviewer start insisting that I run another study that directly tests and replicates my unexpected finding before you’re willing to publish my result, I now actually have something at stake. Because it takes time and money to run new studies, I’m probably not going to bother to follow up on my unexpected finding unless I really believe it. Which is exactly as it should be: I’m the guy who discovered the effect, and I know about all the corners I have or haven’t cut in order to produce it; so if anyone should make the decision about whether to spend more taxpayer money chasing the result, it should be me. You, as the reviewer, are not in a great position to know how plausible the effect truly is, because you have no idea how many different types of analyses I attempted before I got something to ‘work’, or how many failed studies I ran that I didn’t tell you about. Given the huge asymmetry in information, it seems perfectly reasonable for reviewers to say, You think you have a really cool and unexpected effect that you found a compelling story for? Great; go and directly replicate it yourself and then we’ll talk.

“But mistakes happen, and people could get falsely accused!”

Some people don’t like the idea of a guy like Simonsohn running around and busting people’s data fabrication operations for the simple reason that they worry that the kind of approach Simonsohn used to detect fraud is just not that well-tested, and that if we’re not careful, innocent people could get swept up in the net. I think this concern stems from fundamentally good intentions, but once again, I think it’s also misguided.

For one thing, it’s important to note that, despite all the press, Simonsohn hasn’t actually done anything qualitatively different from what other whistleblowers or skeptics have done in the past. He may have suggested new techniques that improve the efficiency with which cheating can be detected, but it’s not as though he invented the ability to report or investigate other researchers for suspected misconduct. Researchers suspicious of other researchers’ findings have always used qualitatively similar arguments to raise concerns. They’ve said things like, hey, look, this is a pattern of data that just couldn’t arise by chance, or, the numbers are too similar across different conditions.

More to the point, perhaps, no one is seriously suggesting that independent observers shouldn’t be allowed to raise their concerns about possible misconduct with journal editors, professional organizations, and universities. There really isn’t any viable alternative. Naysayers who worry that innocent people might end up ensnared by false accusations presumably aren’t suggesting that we do away with all of the existing mechanisms for ensuring accountability; but since the role of people like Simonsohn is only to raise suspicion and provide evidence (and not to do the actual investigating or firing), it’s clear that there’s no way to regulate this type of behavior even if we wanted to (which I would argue we don’t). If I wanted to spend the rest of my life scanning the statistical minutiae of psychology articles for evidence of misconduct and reporting it to the appropriate authorities (and I can assure you that I most certainly don’t), there would be nothing anyone could do to stop me, nor should there be. Remember that accusing someone of misconduct is something anyone can do, but establishing that misconduct has actually occurred is a serious task that requires careful internal investigation. No one–certainly not Simonsohn–is suggesting that a routine statistical test should be all it takes to end someone’s career. In fact, Simonsohn himself has noted that he identified a 4th case of likely fraud that he dutifully reported to the appropriate authorities only to be met with complete silence. Given all the incentives universities and journals have to look the other way when accusations of fraud are made, I suspect we should be much more concerned about the false negative rate than the false positive rate when it comes to fraud.

“But it hurts the public’s perception of our field!”

Sometimes people argue that even if the field does have some serious methodological problems, we still shouldn’t discuss them publicly, because doing so is likely to instill a somewhat negative view of psychological research in the public at large. The unspoken implication being that, if the public starts to lose confidence in psychology, fewer students will enroll in psychology courses, fewer faculty positions will be created to teach students, and grant funding to psychologists will decrease. So, by airing our dirty laundry in public, we’re only hurting ourselves. I had an email exchange with a well-known researcher to exactly this effect a few years back in the aftermath of the Vul et al “voodoo correlations” paper–a paper I commented on to the effect that the problem was even worse than suggested. The argument my correspondent raised was, in effect, that we (i.e., neuroimaging researchers) are all at the mercy of agencies like NIH to keep us employed, and if it starts to look like we’re clowning around, the unemployment rate for people with PhDs in cognitive neuroscience might start to rise precipitously.

While I obviously wouldn’t want anyone to lose their job or their funding solely because of a change in public perception, I can’t say I’m very sympathetic to this kind of argument. The problem is that it places short-term preservation of the status quo above both the long-term health of the field and the public’s interest. For one thing, I think you have to be quite optimistic to believe that some of the questionable methodological practices that are relatively widespread in psychology (data snooping, selective reporting, etc.) are going to sort themselves out naturally if we just look the other way and let nature run its course. The obvious reason for skepticism in this regard is that many of the same criticisms have been around for decades, and it’s not clear that anything much has improved. Maybe the best example of this is Gigerenzer and Sedlmeier’s 1989 paper entitled “Do studies of statistical power have an effect on the power of studies?“, in which the authors convincingly showed that despite three decades of work by luminaries like Jacob Cohen advocating power analyses, statistical power had not risen appreciably in psychology studies. The presence of such unwelcome demonstrations suggests that sweeping our problems under the rug in the hopes that someone (the mice?) will unobtrusively take care of them for us is wishful thinking.

In any case, even if problems did tend to solve themselves when hidden away from the prying eyes of the media and public, the bigger problem with what we might call the “saving face” defense is that it is, fundamentally, an abuse of taxypayers’ trust. As with so many other things, Richard Feynman summed up the issue eloquently in his famous Cargo Cult science commencement speech:

For example, I was a little surprised when I was talking to a friend who was going to go on the radio. He does work on cosmology and astronomy, and he wondered how he would explain what the applications of this work were. “Well,” I said, “there aren’t any.” He said, “Yes, but then we won’t get support for more research of this kind.” I think that’s kind of dishonest. If you’re representing yourself as a scientist, then you should explain to the layman what you’re doing–and if they don’t want to support you under those circumstances, then that’s their decision.

The fact of the matter is that our livelihoods as researchers depend directly on the goodwill of the public. And the taxpayers are not funding our research so that we can “discover” interesting-sounding but ultimately unreplicable effects. They’re funding our research so that we can learn more about the human mind and hopefully be able to fix it when it breaks. If a large part of the profession is routinely employing practices that are at odds with those goals, it’s not clear why taxpayers should be footing the bill. From this perspective, it might actually be a good thing for the field to revise its standards, even if (in the worst-case scenario) that causes a short-term contraction in employment.

“But unreliable effects will just fail to replicate, so what’s the big deal?”

This is a surprisingly common defense of sloppy methodology, maybe the single most common one. It’s also an enormous cop-out, since it pre-empts the need to think seriously about what you’re doing in the short term. The idea is that, since no single study is definitive, and a consensus about the reality or magnitude of most effects usually doesn’t develop until many studies have been conducted, it’s reasonable to impose a fairly low bar on initial reports and then wait and see what happens in subsequent replication efforts.

I think this is a nice ideal, but things just don’t seem to work out that way in practice. For one thing, there doesn’t seem to be much of a penalty for publishing high-profile results that later fail to replicate. The reason, I suspect, is that we incline to give researchers the benefit of the doubt: surely (we say to ourselves), Jane Doe did her best, and we like Jane, so why should we question the work she produces? If we’re really so skeptical about her findings, shouldn’t we go replicate them ourselves, or wait for someone else to do it?

While this seems like an agreeable and fair-minded attitude, it isn’t actually a terribly good way to look at things. Granted, if you really did put in your best effort–dotted all your i’s and crossed all your t’s–and still ended up reporting a false result, we shouldn’t punish you for it. I don’t think anyone is seriously suggesting that researchers who inadvertently publish false findings should be ostracized or shunned. On the other hand, it’s not clear why we should continue to celebrate scientists who ‘discover’ interesting effects that later turn out not to replicate. If someone builds a career on the discovery of one or more seemingly important findings, and those findings later turn out to be wrong, the appropriate attitude is to update our beliefs about the merit of that person’s work. As it stands, we rarely seem to do this.

In any case, the bigger problem with appeals to replication is that the delay between initial publication of an exciting finding and subsequent consensus disconfirmation can be very long, and often spans entire careers. Waiting decades for history to prove an influential idea wrong is a very bad idea if the available alternative is to nip the idea in the bud by requiring stronger evidence up front.

There are many notable examples of this in the literature. A well-publicized recent one is John Bargh’s work on the motor effects of priming people with elderly stereotypes–namely, that priming people with words related to old age makes them walk away from the experiment more slowly. Bargh’s original paper was published in 1996, and according to Google Scholar, has now been cited over 2,000 times. It has undoubtedly been hugely influential in directing many psychologists’ research programs in certain directions (in many cases, in directions that are equally counterintuitive and also now seem open to question). And yet it’s taken over 15 years for a consensus to develop that the original effect is at the very least much smaller in magnitude than originally reported, and potentially so small as to be, for all intents and purposes, “not real”. I don’t know who reviewed Bargh’s paper back in 1996, but I suspect that if they ever considered the seemingly implausible size of the effect being reported, they might have well thought to themselves, well, I’m not sure I believe it, but that’s okay–time will tell. Time did tell, of course; but time is kind of lazy, so it took fifteen years for it to tell. In an alternate universe, a reviewer might have said, well, this is a striking finding, but the effect seems implausibly large; I would like you to try to directly replicate it in your lab with a much larger sample first. I recognize that this is onerous and annoying, but my primary responsibility is to ensure that only reliable findings get into the literature, and inconveniencing you seems like a small price to pay. Plus, if the effect is really what you say it is, people will be all the more likely to believe you later on.

Or take the actor-observer asymmetry, which appears in just about every introductory psychology textbook written in the last 20 – 30 years. It states that people are relatively more likely to attribute their own behavior to situational factors, and relatively more likely to attribute other agents’ behaviors to those agents’ dispositions. When I slip and fall, it’s because the floor was wet; when you slip and fall, it’s because you’re dumb and clumsy. This putative asymmetry was introduced and discussed at length in a book by Jones and Nisbett in 1971, and hundreds of studies have investigated it at this point. And yet a 2006 meta-analysis by Malle suggested that the cumulative evidence for the actor-observer asymmetry is actually very weak. There are some specific circumstances under which you might see something like the postulated effect, but what is quite clear is that it’s nowhere near strong enough an effect to justify being routinely invoked by psychologists and even laypeople to explain individual episodes of behavior. Unfortunately, at this point it’s almost impossible to dislodge the actor-observer asymmetry from the psyche of most researchers–a reality underscored by the fact that the Jones and Nisbett book has been cited nearly 3,000 times, whereas the 1996 meta-analysis has been cited only 96 times (a very low rate for an important and well-executed meta-analysis published in Psychological Bulletin).

The fact that it can take many years–whether 15 or 45–for a literature to build up to the point where we’re even in a position to suggest with any confidence that an initially exciting finding could be wrong means that we should be very hesitant to appeal to long-term replication as an arbiter of truth. Replication may be the gold standard in the very long term, but in the short and medium term, appealing to replication is a huge cop-out. If you can see problems with an analysis right now that cast aspersions on a study’s results, it’s an abdication of responsibility to downplay your concerns and wait for someone else to come along and spend a lot more time and money trying to replicate the study. You should point out now why you have concerns. If the authors can address them, the results will look all the better for it. And if the authors can’t address your concerns, well, then, you’ve just done science a service. If it helps, don’t think of it as a matter of saying mean things about someone else’s work, or of asserting your own ego; think of it as potentially preventing a lot of very smart people from wasting a lot of time chasing down garden paths–and also saving a lot of taxpayer money. Remember that our job as scientists is not to make other scientists’ lives easy in the hopes they’ll repay the favor when we submit our own papers; it’s to establish and apply standards that produce convergence on the truth in the shortest amount of time possible.

“But it would hurt my career to be meticulously honest about everything I do!”

Unlike the other considerations listed above, I think the concern that being honest carries a price when it comes to do doing research has a good deal of merit to it. Given the aforementioned delay between initial publication and later disconfirmation of findings (which even in the best case is usually longer than the delay between obtaining a tenure-track position and coming up for tenure), researchers have many incentives to emphasize expediency and good story-telling over accuracy, and it would be disingenuous to suggest otherwise. No malevolence or outright fraud is implied here, mind you; the point is just that if you keep second-guessing and double-checking your analyses, or insist on routinely collecting more data than other researchers might think is necessary, you will very often find that results that could have made a bit of a splash given less rigor are actually not particularly interesting upon careful cross-examination. Which means that researchers who have, shall we say, less of a natural inclination to second-guess, double-check, and cross-examine their own work will, to some degree, be more likely to publish results that make a bit of a splash (it would be nice to believe that pre-publication peer review filters out sloppy work, but empirically, it just ain’t so). So this is a classic tragedy of the commons: what’s good for a given individual, career-wise, is clearly bad for the community as a whole.

I wish I had a good solution to this problem, but I don’t think there are any quick fixes. The long-term solution, as many people have observed, is to restructure the incentives governing scientific research in such a way that individual and communal benefits are directly aligned. Unfortunately, that’s easier said than done. I’ve written a lot both in papers (1, 2, 3) and on this blog (see posts linked here) about various ways we might achieve this kind of realignment, but what’s clear is that it will be a long and difficult process. For the foreseeable future, it will continue to be an understandable though highly lamentable defense to say that the cost of maintaining a career in science is that one sometimes has to play the game the same way everyone else plays the game, even if it’s clear that the rules everyone plays by are detrimental to the communal good.

 

Anyway, this may all sound a bit depressing, but I really don’t think it should be taken as such. Personally I’m actually very optimistic about the prospects for large-scale changes in the way we produce and evaluate science within the next few years. I do think we’re going to collectively figure out how to do science in a way that directly rewards people for employing research practices that are maximally beneficial to the scientific community as a whole. But I also think that for this kind of change to take place, we first need to accept that many of the defenses we routinely give for using iffy methodological practices are just not all that compelling.

tracking replication attempts in psychology–for real this time

I’ve written a few posts on this blog about how the development of better online infrastructure could help address and even solve many of the problems psychologists and other scientists face (e.g., the low reliability of peer review, the ‘fudge factor’ in statistical reporting, the sheer size of the scientific literature, etc.). Actually, that general question–how we can use technology to do better science–occupies a good chunk of my research these days (see e.g., Neurosynth). One question I’ve been interested in for a long time is how to keep track not only of ‘successful’ studies (i.e., those that produce sufficiently interesting effects to make it into the published literature), but also replication failures (or successes of limited interest) that wind up in researchers’ file drawers. A couple of years ago I went so far as to build a prototype website for tracking replication attempts in psychology. Unfortunately, it never went anywhere, partly (okay, mostly) because the site really sucked, and partly because I didn’t really invest much effort in drumming up interest (mostly due to lack of time). But I still think the idea is a valuable one in principle, and a lot of other people have independently had the same idea (which means it must be right, right?).

Anyway, it looks like someone finally had the cleverness, time, and money to get this right. Hal Pashler, Sean Kang*, and colleagues at UCSD have been developing an online database for tracking attempted replications of psychology studies for a while now, and it looks like it’s now in beta. PsychFileDrawer is a very slick, full-featured platform that really should–if there’s any justice in the world–provide the kind of service everyone’s been saying we need for a long time now. If it doesn’t work, I think we’ll have some collective soul-searching to do, because I don’t think it’s going to get any easier than this to add and track attempted replications. So go use it!

 

*Full disclosure: Sean Kang is a good friend of mine, so I’m not completely impartial in plugging this (though I’d do it anyway). Sean also happens to be amazingly smart and in search of a faculty job right now. If I were you, I’d hire him.

the ‘decline effect’ doesn’t work that way

Over the last four or five years, there’s been a growing awareness in the scientific community that science is an imperfect process. Not that everyone used to think science was a crystal ball with a direct line to the universe or anything, but there does seem to be a growing recognition that scientists are human beings with human flaws, and are susceptible to common biases that can make it more difficult to fully trust any single finding reported in the literature. For instance, scientists like interesting results more than boring results; we’d rather keep our jobs than lose them; and we have a tendency to see what we want to see, even when it’s only sort-of-kind-of there, and sometimes not there at all. All of these things contrive to produce systematic biases in the kinds of findings that get reported.

The single biggest contributor to the zeitgeist shift nudge is undoubtedly John Ioannidis (recently profiled in an excellent Atlantic article), whose work I can’t say enough good things about (though I’ve tried). But lots of other people have had a hand in popularizing the same or similar ideas–many of which actually go back several decades. I’ve written a bit about these issues myself in a number of papers (1, 2, 3) and blog posts (1, 2, 3, 4, 5), so I’m partial to such concerns. Still, important as the role of the various selection and publication biases is in charting the course of science, virtually all of the discussions of these issues have had a relatively limited audience. Even Ioannidis’ work, influential as it’s been, has probably been read by no more than a few thousand scientists.

Last week, the debate hit the mainstream when the New Yorker (circulation: ~ 1 million) published an article by Jonah Lehrer suggesting–or at least strongly raising the possibility–that something might be wrong with the scientific method. The full article is behind a paywall, but I can helpfully tell you that some people seem to have un-paywalled it against the New Yorker’s wishes, so if you search for it online, you will find it.

The crux of Lehrer’s argument is that many, and perhaps most, scientific findings fall prey to something called the “decline effect”: initial positive reports of relatively large effects are subsequently followed by gradually decreasing effect sizes, in some cases culminating in a complete absence of an effect in the largest, most recent studies. Lehrer gives a number of colorful anecdotes illustrating this process, and ends on a decidedly skeptical (and frankly, terribly misleading) note:

The decline effect is troubling because it reminds us how difficult it is to prove anything. We like to pretend that our experiments define the truth for us. But that’s often not the case. Just because an idea is true doesn’t mean it can be proved. And just because an idea can be proved doesn’t mean it’s true. When the experiments are done, we still have to choose what to believe.

While Lehrer’s article received pretty positive reviews from many non-scientist bloggers (many of whom, dismayingly, seemed to think the take-home message was that since scientists always change their minds, we shouldn’t trust anything they say), science bloggers were generally not very happy with it. Within days, angry mobs of Scientopians and Nature Networkers started murdering unicorns; by the end of the week, the New Yorker offices were reduced to rubble, and the scientists and statisticians who’d given Lehrer quotes were all rumored to be in hiding.

Okay, none of that happened. I’m just trying to keep things interesting. Anyway, because I’ve been characteristically lazy slow on the uptake, by the time I got around to writing this post you’re now reading, about eighty hundred and sixty thousand bloggers had already weighed in on Lehrer’s article. That’s good, because it means I can just direct you to other people’s blogs instead of having to do any thinking myself. So here you go: good posts by Games With Words (whose post tipped me off to the article), Jerry Coyne, Steven Novella, Charlie Petit, and Andrew Gelman, among many others.

Since I’ve blogged about these issues before, and agree with most of what’s been said elsewhere, I’ll only make one point about the article. Which is that about half of the examples Lehrer talks about don’t actually seem to me to qualify as instances of the decline effect–at least as Lehrer defines it. The best example of this comes when Lehrer discusses Jonathan Schooler’s attempt to demonstrate the existence of the decline effect by running a series of ESP experiments:

In 2004, Schooler embarked on an ironic imitation of Rhine’s research: he tried to replicate this failure to replicate. In homage to Rhirie’s interests, he decided to test for a parapsychological phenomenon known as precognition. The experiment itself was straightforward: he flashed a set of images to a subject and asked him or her to identify each one. Most of the time, the response was negative—-the images were displayed too quickly to register. Then Schooler randomly selected half of the images to be shown again. What he wanted to know was whether the images that got a second showing were more likely to have been identified the first time around. Could subsequent exposure have somehow influenced the initial results? Could the effect become the cause?

The craziness of the hypothesis was the point: Schooler knows that precognition lacks a scientific explanation. But he wasn’t testing extrasensory powers; he was testing the decline effect. “At first, the data looked amazing, just as we’d expected,“ Schooler says. “I couldn’t believe the amount of precognition we were finding. But then, as we kept on running subjects, the effect size“–a standard statistical measure–“kept on getting smaller and smaller.“ The scientists eventually tested more than two thousand undergraduates. “In the end, our results looked just like Rhinos,“ Schooler said. “We found this strong paranormal effect, but it disappeared on us.“

This is a pretty bad way to describe what’s going on, because it makes it sound like it’s a general principle of data collection that effects systematically get smaller. It isn’t. The variance around the point estimate of effect size certainly gets smaller as samples get larger, but the likelihood of an effect increasing is just as high as the likelihood of it decreasing. The absolutely critical point Lehrer left out is that you would only get the decline effect to show up if you intervened in the data collection or reporting process based on the results you were getting. Instead, most of Lehrer’s article presents the decline effect as if it’s some sort of mystery, rather than the well-understood process that it is. It’s as though Lehrer believes that scientific data has the magical property of telling you less about the world the more of it you have. Which isn’t true, of course; the problem isn’t that science is malfunctioning, it’s that scientists are still (kind of!) human, and are susceptible to typical human biases. The unfortunate net effect is that Lehrer’s article, while tremendously entertaining, achieves exactly the opposite of what good science journalism should do: it sows confusion about the scientific process and makes it easier for people to dismiss the results of good scientific work, instead of helping people develop a critical appreciation for the amazing power science has to tell us about the world.