Evaluating a new critique of the Reproducibility Project

Over the last five years psychologists have been paying more and more attention to issues that could be diminishing the quality of our published research — things like low power, p-hacking, and publication bias. We know these things can affect reproducibility, but it can be hard to gauge their practical impact. The Reproducibility Project: Psychology (RPP), published last year in Science, was a massive, coordinated effort to produce an estimate of where several of the field’s top journals stood in 2008 before all the attention and concerted improvement began.

The RPP is not perfect, and the paper is refreshingly frank about its limitations and nuanced about its conclusions. But all science proceeds on fallible evidence (there isn’t any other kind), and it has been welcomed by many psychologists as an informative examination of the reliability of our published findings.

Welcomed by many, but not welcomed by all.

In a technical commentary released today in Science, Dan Gilbert, Gary King, Stephen Pettigrew, and Tim Wilson take exception to the conclusions that the RPP authors and many scientists who read it have reached. They offer re-analyses of the RPP, some incorporating outside data. They maintain that the RPP authors’ conclusions are wrong, and on re-examination the data tell us that “the reproducibility of psychological science is quite high.” (The RPP authors published a reply.)

What should we make of it? I read the technical comment, the supplement (as you’ll see there were some surprises in it), the Open Science Collaboration’s reply, Gilbert et al.’s unpublished response to the reply, and I re-read the Many Labs report that plays a critical role in the commentary. Here are my thoughts.

Unpacking the critics’ replication metric

To start with, a key to understanding Gilbert et al.’s critique is understanding the metric of replicability that it uses.

There are many reasons why original and replication studies might get different results. Some are neutral and unavoidable, like sampling error. Some are signs of good things, like scientists pushing into the unknown. But some are problems. That can include a variety of errors and biases in original studies, errors and biases in replications, and systemic problems like publication bias. Just like there are many reasons for originals and replications to get different results, there are many ways to index those differences. Different metrics are sensitive to different things about original and replication studies. Whereas the RPP looked at a number of different metrics, the critique focuses on one: whether the point estimate of the replication effect size falls within the confidence interval of the original.

But in justifying this choice, the critique’s authors misstate what confidence intervals are. They write that 95% of replications should fall within the original studies’ confidence intervals. That just isn’t true – a P% confidence interval does not predict P% success in future replications. To be fair, almost everyone misinterprets confidence intervals. But when they are pivotal to your sole metric of reproducibility and your interpretation hinges on them, it would be good to get them right.

Another issue that is critical to interpreting intervals is knowing that intervals get wider the less data you have. This is never addressed, but the way Gilbert et al. use original studies’ confidence intervals to gauge replicability means that the lower an original study’s power, the easier it will be to “successfully” replicate it. Conversely, a very high-powered original study can “fail to replicate” because of trivial heterogeneity in the effect. Not all replication metrics are vulnerable to this problem. But if you are going to use a replication metric that is sensitive to power in this way, you need to present it alongside other information that puts it in context. Otherwise you can be led seriously astray.

A limited scope with surprising omissions

The RPP is descriptive, observational data about replications. Gilbert et al. try to model the underlying causes. If there are many reasons why original and replication studies can differ, it would make sense to try to model as many of them as possible, or at least the most important ones. Unfortunately, the critique takes a quite narrow, confirmatory approach to modeling differences between original and replication studies. Of all the possible reasons why original and replication studies can differ, it only looks for random error and flaws in replication studies.

This leads to some striking omissions. For example, any scientist can tell you that publication bias is ubiquitous. It creates biases in the results of original published studies, which can make it harder to reproduce their (biased) effects. But it would not have affected the replications in the RPP. Nor would it affect the comparisons among Many Labs replications that Gilbert et al. use as benchmarks (more on that in a moment). Yet the commentary’s re-analyses of replicability make no attempt to detect or account for publication bias anywhere.

If you want to know how much something varies, calculate its variance

Gilbert et al. propose that replications might have variable effects because of differences in study populations or procedures. This is certainly an important issue, and one that has been raised before in interpreting replications.

In order to offer new insight on this issue, Gilbert et al. re-analyze data from Klein et al.’s (2014) Many Labs 1 study to see how often pairs of studies trying to get the same effect had a “successful” replication by the original-study-confidence-interval criterion. Unfortunately, that analysis mixes together power and effect size heterogeneity – they are very different things, and both higher power of original studies and effect size heterogeneity will lower replication success in this kind of analysis. It does not provide a clean estimate of effect variability.

There is a more straightforward way to know if effects varied across Many Labs replication sites: calculate the variance in the effects. Klein et al. report this in their Table 3. The data show that big effects tended to vary across sites but more modest ones did not. And by big I mean big – there are 5 effects in Many Labs 1 with a Cohen’s d greater than 1.0. Four of them are variations on the anchoring effect. Effect sizes that big are quite unusual in social psychology – they were probably included by Klein et al. to make sure there were some slam-dunk effects in the Many Labs project, not because they are representative. But effects that are more typical in size are not particularly variable in Many Labs 1. Nor is there much variance in any of the effects examined in the similar Many Labs 3.

Apples-to-oranges comparisons of replicability from RPP to Many Labs

Another argument Gilbert et al. make is that with enough power, most RPP replications would have been successful. To support this argument they look again at Many Labs to see how often the combined sample of 6000+ participants could replicate the original studies. Here is how they describe it:

OSC attempted to replicate each of 100 studies just once, and that attempt produced an unsettling result: Only 47% of the original studies were successfully replicated (i.e., produced effects that fell within the confidence interval of the original study). In contrast, MLP [Many Labs] attempted to replicate each of its studies 35 or 36 times and then pooled the data. MLP’s much more powerful method produced a much more heartening result: A full 85% of the original studies were successfully replicated. What would have happened to MLP’s heartening result if they had used OSC’s method? Of MLP’s 574 replication studies, only 195 produced effects that fell within the confidence interval of the original, published study. In other words, if MLP had used OSC’s method, they would have reported an unsettling replication rate of 34% rather than the heartening 85% they actually reported.

Three key numbers stand out in this paragraph. The RPP replication rate was 47%. The high-powered (N>6000) Many Labs pooled-sample replication rate was 85%. But if the RPP approach is applied to Many Labs (i.e. looking at single samples instead of the pooled rate), the rate drops to 34%. On its face, that sound like a problem for the RPP.

Except when I actually looked at Table 2 of Many Labs and tried to verify the 85% number for the pooled sample, I couldn’t. There are 15 original studies where a confidence interval could be calculated. Only 6 of the pooled replication effects landed inside the intervals. So the correct number is 40%. Where did 85% come from? Although it’s virtually impossible to tell in the paragraph I quoted above, I found buried in the supplement the key detail that Gilbert et al. got their “heartening” 85% from a totally different replication metric — the tally of of replications that got p < .05 (if you treat the anchoring effects as one, there are 11 significant effects out of 13). Instead of making an apples-to-apples comparison, they switch to a different metric exactly once in their critique, on only one side of this key comparison.

What if instead you calculate the replicability rate using the same metric for both sides of the comparison? Using the confidence interval metric that Gilbert et al. use everywhere else, you get 47% in the RPP versus 40% in the pooled analysis of Many Labs. So the RPP actually did better than Many Labs with its N > 6000 sample sizes. How could that be?

It turns out that the confidence interval metric can lead you to some surprising conclusions. Because larger effects were more variable in Many Labs 1, the effects that did the worst job “replicating” by Gilbert et al’s original-study-confidence-interval criterion are the biggest ones. Thus anchoring – yes, anchoring – “failed to replicate” three out of four times. Gain vs. loss framing failed too. (Take that, Kahneman and Tversky!) By contrast, flag priming would appear to have replicated successfully – even though the original authors themselves have said that Many Labs did not successfully replicate it.

In addition to completely undermining the critique’s conclusion about power, all of this goes back to my earlier point that the confidence-interval metric needs to be interpreted with great caution. In the RPP authors’ reply, they mention bring up differences among replication metrics. In an unpublished response, Gilbert et al. write: “This is a red herring. Neither we nor the authors of OSC­2015 found any substantive differences in the conclusions drawn from the confidence interval measure versus the other measures.” I don’t know what to make of that. How can they think 85% versus 40% is not a substantive difference?

Flaws in a fidelity metric

Another issue raised by the critique is what its authors call the “fidelity” of the replications: how well the replication protocols got the original studies’ methods right. As with variability in populations and procedures, this is an important issue that merits a careful look in any replication study.

The technical comment gives a few examples of differences between original and replication protocols that sound to like they could have mattered in some casese. How did these issues play out in the RPP as a whole? Unfortunately, the critique uses a flawed metric to quantify the effects of fidelity: the original authors’ endorsement of the replication protocol.

There are two problems with their approach. First, original study authors have expertise in the methods, of course. But they also have inside knowledge about flaws in their original studies. The critique acknowledges this problem but makes no attempt to account for it in the analyses.

Second, Gilbert et al. compared “endorsements” to “nonendorsements,” but a majority of the so-called nonendorsements were cases where original authors simply did not respond – an important detail that is again only found in the supplement. Original authors only registered concerns in 11 out of 100 replications, versus 18 nonresponses. Like with any missing-data problem, we do not know what the nonresponders would have said if they had responded. But the analysis assumes that none of the 18 would have endorsed the replication protocols.

A cleaner fidelity metric would have helped. But ultimately, these kinds of indirect analyses can only go so far. Gilbert et al. claim that original studies would replicate just fine if only replicators would get the procedures right. This is an empirical question with a very direct way of getting an answer: go run a replication the way you think it ought to be done. I suspect that some of the studies probably would successfully replicate, either because of Type II error or substantive differences. We could learn a tremendous amount from direct empirical tests of hypotheses about replication fidelity and other hidden moderators, far more than we can from these kinds of indirect analyses with weak proxies.

We can move the conversation forward

In the last 5 years there have been a lot of changes in psychology. We now know that there are problems with how we have sometimes done research in the past. For example, it was long considered okay to analyze small, noisy datasets with a lot of flexibility to look around for patterns that supported a publishable conclusion. There is a lot more awareness now that these practices will lead to lower reproducibility, and the field is starting to do something about that. The RPP came around after we already knew that. But it added meaningfully to that discussion by giving us an estimate of reproducibility in several top journals. It gave us a sense, however rough, of where the field stood in 2008 before we started making changes.

That does not mean psychologists are all of one mind about where psychology is at on reproducibility and what we ought to do about it. There has been a lot of really fruitful discussion recently coming from different perspectives. Some of the critical commentaries raise good concerns and have a lot of things I agree with.

The RPP was a big and complicated project, and given its impact it warrants serious critical analysis from multiple perspectives. I agree with Uri Simonsohn that some of the protocol differences between originals and replications deserve closer scrutiny, and it is good that Gilbert et al. brought them to our attention. I found myself less enthusiastic about their analyses, for the reasons I have outlined here.

But the discussion will continue to move forward. The RPP dataset is still open, and I know there are other efforts under way to draw new insights from it. Even better, there is lots of other, new meta-science happening too. I remain optimistic that as we continue to learn more, we will keep making things better in our field.

* * * * *

UPDATE (3/8/2016): There has been a lot of discussion about the Gilbert et al. technical comment since I put up this blog. Gilbert et al. have written a reply that responds to some of the issues that I and others have raised.

Here are some other relevant discussions in the academic blogosphere:

Moderator interpretations of the Reproducibility Project

The Reproducibility Project: Psychology (RPP) was published in Science last week. There has been some excellent coverage and discussion since then. If you haven’t heard about it,* Ed Yong’s Atlantic coverage will catch you up. And one of my favorite commentaries so far is on Michael Frank’s blog, with several very smart and sensible ways the field can proceed next.

Rather than offering a broad commentary, in this post I’d like to discuss one possible interpretation of the results of the RPP, which is “hidden moderators.” Hidden moderators are unmeasured differences between original and replication experiments that would result in differences in the true, underlying effects and therefore in the observed results of replications. Things like differences in subject populations and experimental settings. Moderator interpretations were the subject of a lengthy discussion on the ISCON Facebook page recently, and are the focus of an op-ed by Lisa Feldman Barrett.

In the post below, I evaluate the hidden-moderator interpretation. The tl;dr version is this: Context moderators are probably common in the world at large and across independently-conceived experiments. But an explicit design goal of direct replication is to eliminate them, and there’s good reason to believe they are rare in replications.

1. Context moderators are probably not common in direct replications

Many social and personality psychologists believe that lots of important effects vary by context out in the world at large. I am one of those people — subject and setting moderators are an important part of what I study in my own work. William McGuire discussed the idea quite eloquently, and it can be captured in an almost koan-like quote from Niels Bohr: “The opposite of one profound truth may very well be another profound truth.” It is very often the case that support for a broad hypothesis will vary and even be reversed over traditional “moderators” like subjects and settings, as well as across different methods and even different theoretical interpretations.

Consider as a thought experiment** what would happen if you told 30 psychologists to go test the deceptively simple-seeming hypothesis “Happiness causes smiling” and turned them loose. You would end up with 30 different experiments that would differ in all kinds of ways that we can be sure would matter: subjects (with different cultural norms of expressiveness), settings (e.g., subjects run alone vs. in groups), manipulations and measures of the IV (film clips, IAPS pictures, frontal asymmetry, PANAS?) and DV (FACS, EMG, subjective ratings?), and even construct definitions (state or trait happiness? eudaimonic or hedonic? Duchenne or social smiles?). You could learn a lot by studying all the differences between the experiments and their results.

But that stands in stark contrast to how direct replications are carried out, including the RPP. Replicators aren’t just turned loose with a broad hypothesis. In direct replication, the goal is to test the hypothesis “If I do the same experiment, I will get the same result.” Sometimes a moderator-ish hypothesis is built in (“this study was originally done with college students, will I get the same effect on Mturk?”). But such differences from the original are planned in. The explicit goal of replication design is for any other differences to be controlled out. Well-designed replication research makes a concerted effort to faithfully repeat the original experiments in every way that documentation, expertise, and common sense say should matter (and often in consultation with original authors too). The point is to squeeze out any room for substantive differences.

Does it work? In a word, yes. We now have data telling us that the squeezing can be very effective. In Many Labs 1 and Many Labs 3 (which I reviewed here), different labs followed standardized replication protocols for a series of experiments. In principle, different experimenters, different lab settings, and different subject populations could have led to differences between lab sites. But in analyses of heterogeneity across sites, that was not the result. In ML1, some of the very large and obvious effects (like anchoring) varied a bit in just how large they were (from “kinda big” to “holy shit”). Across both projects, more modest effects were quite consistent. Nowhere was there evidence that interesting effects wink in and out of detectability for substantive reasons linked to sample or setting.

We will continue to learn more as our field gets more experience with direct replication. But right now, a reasonable conclusion from the good, systematic evidence we have available is this: When some researchers write down a good protocol and other researchers follow it, the results tend to be consistent. In the bigger picture this is a good result for social psychology: it is empirical evidence that good scientific control is within our reach, neither beyond our experimental skills nor intractable for the phenomena we study.***

But it also means that when replicators try to clamp down potential moderators, it is reasonable to think that they usually do a good job. Remember, the Many Labs labs weren’t just replicating the original experiments (from which their results sometimes differed – more on that in a moment). They were very successfully and consistently replicating each other. There could be individual exceptions here and there, but on the whole our field’s experience with direct replication so far tells us that it should be unusual for unanticipated moderators to escape replicators’ diligent efforts at standardization and control.

2. A comparison of a published original and a replication is not a good way to detect moderators

Moderation means there is a substantive difference between 2 or more (true, underlying) effects as a function of the moderator variable. When you design an experiment to test a moderation hypothesis, you have to set things up so you can make a valid comparison. Your observations should ideally be unbiased, or failing that, the biases should be the same at different levels of the moderator so that they cancel out in the comparison.

With the RPP (and most replication efforts), we are trying to interpret observed differences between published original results and replications. The moderator interpretation rests on the assumption that observed differences between experiments are caused by substantive differences between them (subjects, settings, etc.). An alternative explanation is that there are different biases. And that is almost certainly the case. The original experiments are generally noisier because of modest power, and that noise is then passed through a biased filter (publication bias for sure — these studies were all published at selective journals — and perhaps selective reporting in some cases too). By contrast, the replications are mostly higher powered, the analysis plans were pre-registered, and the replicators committed from the outset to publish their findings no matter what the results.

That means that a comparison of published original studies and replication studies in the RPP is a poor way to detect moderators, because you are comparing a noisy and biased observation to one that is much less so.**** And such a comparison would be a poor way to detect moderators even if you were quite confident that moderators were out there somewhere waiting to be found.

3. Moderator explanations of the Reproducibility Project are (now) post hoc

The Reproducibility Project has been conducted with an unprecedented degree of openness. It was started 4 years ago. Both the coordinating plan and the protocols of individual studies were pre-registered. The list of selected studies was open. Original authors were contacted and invited to consult.

What that means is that anyone could have looked at an original study and a replication protocol, applied their expert judgment, and made a genuinely a priori prediction of how the replication results would have differed from the original. Such a prediction could have been put out in the open at any time, or it could have been pre-registered and embargoed so as not to influence the replication researchers.

Until last Friday, that is.

Now the results of the RPP are widely known. And although it is tempting to now look back selectively at “failed” replications and generate substantively interesting reasons, such explanations have to be understood for what they are: untested post hoc speculation. (And if someone now says they expected a failure all along, they’re possibly HARKing too.)

Now, don’t get me wrong — untested post hoc speculation is often what inspires new experiments. So if someone thinks they see an important difference between an original result and a replication and gets an idea for a new study to test it out, more power to them. Get thee to the lab.

But as an interpretation of the data we have in front of us now, we should be clear-eyed in appraising such explanations, especially as an across-the-board factor for the RPP. From a bargain-basement Bayesian perspective, context moderators in well-controlled replications have a low prior probability (#1 above), and comparisons of original and replication studies have limited evidential value because of unequal noise and bias (#2). Put those things together and the clear message is that we should be cautious about concluding that there are hidden moderators lurking everywhere in the RPP. Here and there, there might be compelling, idiosyncratic reasons to think there could be substantive differences to motivate future research. But on the whole, as an explanation for the overall pattern of findings, hidden moderators are not a strong contender.

Instead, we need to face up to the very well-understood and very real differences that we know about between published original studies and replications. The noxious synergy between low power and selective publication is certainly a big part of the story. Fortunately, psychology has already started to make changes since 2008 when the RPP original studies were published. And positive changes keep happening.

Would it be nice to think that everything was fine all along? Of course. And moderator explanations are appealing because they suggest that everything is fine, we’re just discovering limits and boundary conditions like we’ve always been doing.***** But it would be counterproductive if that undermined our will to continue to make needed improvements to our methods and practices. Personally, I don’t think everything in our past is junk, even post-RPP – just that we can do better. Constant self-critique and improvement are an inherent part of science. We have diagnosed the problem and we have a good handle on the solution. All of that makes me feel pretty good.


* Seriously though?

** A thought meta-experiment? A gedankengedankenexperiment?

*** I think if you asked most social psychologists, divorced from the present conversation about replicability and hidden moderators, they would already have endorsed this view. But it is nice to have empirical meta-scientific evidence to support it. And to show the “psychology isn’t a science” ninnies.

**** This would be true even if you believed that the replicators were negatively biased and consciously or unconsciously sandbagged their efforts. You’d think the bias was in the other direction, but it would still be unequal and therefore make comparisons of original vs. replication a poor empirical test of moderation. (You’d also be a pretty cynical person, but anyway.)

***** For what it’s worth, I’m not so sure that the hidden moderator interpretation would actually be all that reassuring under the cold light of a rational analysis. This is not the usual assumption that moderators are ubiquitous out in the world. We are talking about moderators that pop up despite concerted efforts to prevent them. Suppose that ubiquitous occult moderators were the sole or primary explanation for the RPP results — so many effects changing when we change so little, going from one WEIRD sample to another, with maybe 5-ish years of potential for secular drift, and using a standardized protocol. That would suggest that we have a poor understanding of what is going on in our labs. It would also suggest that it is extraordinarily hard to study main effects or try to draw even tentative generalizable conclusions about them. And given how hard it is to detect interactions, that would mean that our power problem would be even worse than people think it is now.