Reading “The Baby Factory” in context

cherry orchard
Photo credit: Des Blenkinsopp.

Yesterday I put up a post about David Peterson’s ethnography The Baby Factory, an ethnography of 3 baby labs that discusses Peterson’s experience as a participant observer. My post was mostly excerpts, with a short introduction at the beginning and a little discussion at the end. That was mostly to encourage people to go read it. (It’s open-access!)

Today I’d like to say a little more.

How you approach the article probably depends a lot on what background and context you come to it with. It would be a mistake to look to an ethnography for a generalizable estimate of something about a population, in this case about how common various problematic practices are. That’s not what ethnography is for. But at this point in history, we are not lacking for information about the ways we need to improve psychological science. There have been surveys and theoretical analyses and statistical analyses and single-lab replications and coordinated many-lab replications and all the rest. It’s getting harder and harder to claim that the evidence is cherry-picked without seriously considering the possibility that you’re in the middle of a cherry orchard. As Simine put it so well:

even if you look at your own practices and those of everyone you know, and you don’t see much p-hacking going on, the evidence is becoming overwhelming that p-hacking is happening a lot. my guess is that the reason people can’t reconcile that with the practices they see happening in their labs and their friends’ labs is that we’re not very good at recognizing p-hacking when it’s happening, much less after the fact. we can’t rely on our intuitions about p-hacking. we have to face the facts. and, in my view, the facts are starting to look pretty damning.

You don’t even have to go as far as Simine or me. You just have to come into reading the ethnography with a realistic belief that problematic practices are at least at a high enough rate to be worrisome. And then the ethnography does what ethnographies do, and well in my judgment: it illustrates what these things look like, out there in the world, when they are happening.

In particular, I think a valuable part of Peterson’s ethnography is that it shows how problematic practices don’t just have to happen furtively by one person with the door closed. Instead, they can work their way into the fabric of how members of a lab talk and interact. When Leslie John et al. introduced the term questionable research practices, they defined it as “exploitation of the gray area of acceptable practice.” The Baby Factory gives us a view into how that can be a social process. Gray zones are by definition ambiguous; should we be shocked to find out that people working closely together will come to a socially shared understanding of them?

Another thing Peterson’s ethnography does is talk about the larger context where all this is happening, and try to interpret his observations in that context. He writes about the pressures for creating a public narrative of science that looks sharp and clean, about the need to make the most of very limited resources and opportunities, and about the very real challenges of working with babies (the “difficult research objects” of the subtitle). A commenter yesterday thought he came to the project with an axe to grind. But his interpretive framing was very sympathetic to the challenges of doing infant cognition research. And his concluding paragraphs were quite optimistic, suggesting that the practices he observed may be part of a “local culture” that has figured out how they can promote positive scientific development. I wish he’d developed that argument more. I don’t think infant cognition research has lacked for important scientific discoveries — but I would say it is in spite of the compromises researchers have sometimes had to make, not because of them.

I do think it would be a mistake to come away thinking this is something limited to infant cognition research. Peterson grounds his discussion in the specific challenges of studying babies, who have a habit of getting distracted or falling asleep or putting your stimuli in their mouths. Those particular problems may be distinctive to having babies as subjects, and I can understand why that framing might make baby researchers feel especially uncomfortable. But anybody who is asking big questions about the human mind is working with a difficult research object, and we all face the same larger pressures and challenges. There are some great efforts under way to understand the particular challenges of research practice and replicability in infant research, but whatever we learn from that is going to be about how broader problems are manifesting in a specific area. I don’t really see how you can fairly conclude otherwise.

An eye-popping ethnography of three infant cognition labs

I don’t know how else to put it. David Peterson, a sociologist, recently published an ethnographic study of 3 infant cognition labs. Titled “The Baby Factory: Difficult Research Objects, Disciplinary Standards, and the Production of Statistical Significance,” it recounts his time spend as a participant observer in those labs, attending lab meetings and running subjects.

In his own words, Peterson “shows how psychologists produce statistically significant results under challenging circumstances by using strategies that enable them to bridge the distance between an uncontrollable research object and a professional culture that prizes methodological rigor.” The account of how the labs try to “bridge the distance” reveals one problematic practice after another, in a way that sometimes makes them seem like normal practice and no big deal to the people in the labs. Here are a few examples.

Protocol violations that break blinding and independence:

…As a routine part of the experiments, parents are asked to close their eyes to prevent any unconscious influence on their children. Although this was explicitly stated in the instructions given to parents, during the actual experiment, it was often overlooked; the parents’ eyes would remain open. Moreover, on several occasions, experimenters downplayed the importance of having one’s eyes closed. One psychologist told a mother, “During the trial, we ask you to close your eyes. That’s just for the journals so we can say you weren’t directing her attention. But you can peek if you want to. It’s not a big deal. But there’s not much to see.”

Optional stopping based on data peeking:

Rather than waiting for the results from a set number of infants, experimenters began “eyeballing” the data as soon as babies were run and often began looking for statistical significance after just 5 or 10 subjects. During lab meetings and one-on-one discussions, experiments that were “in progress” and still collecting data were evaluated on the basis of these early results. When the preliminary data looked good, the test continued. When they showed ambiguous but significant results, the test usually continued. But when, after just a few subjects, no significance was found, the original protocol was abandoned and new variations were developed.

Invalid comparisons of significant to nonsignificant:

Because experiments on infant subjects are very costly in terms of both time and money, throwing away data is highly undesirable. Instead, when faced with a struggling experiment using a trusted experimental paradigm, experimenters would regularly run another study that had higher odds of success. This was accomplished by varying one aspect of the experiment, such as the age of the participants. For instance, when one experiment with 14-month-olds failed, the experimenter reran the same study with 18-month-olds, which then succeeded. Once a significant result was achieved, the failures were no longer valueless. They now represented a part of a larger story: “Eighteen-month-olds can achieve behavior X, but 14-month-olds cannot.” Thus, the failed experiment becomes a boundary for the phenomenon.

And HARKing:

When a clear and interesting story could be told about significant findings, the original motivation was often abandoned. I attended a meeting between a graduate student and her mentor at which they were trying to decipher some results the student had just received. Their meaning was not at all clear, and the graduate student complained that she was having trouble remembering the motivation for the study in the first place. Her mentor responded, “You don’t have to reconstruct your logic. You have the results now. If you can come up with an interpretation that works, that will motivate the hypothesis.”

A blunt explanation of this strategy was given to me by an advanced graduate student: “You want to know how it works? We have a bunch of half-baked ideas. We run a bunch of experiments. Whatever data we get, we pretend that’s what we were looking for.” Rather than stay with the original, motivating hypothesis, researchers in developmental science learn to adjust to statistical significance. They then “fill out” the rest of the paper around this necessary core of psychological research.

Peterson discusses all this in light of recent discussions about replicability and scientific practices in psychology. He says that researchers have basically 3 choices: limit the scope of your questions to what you can do well with available methods, relax our expectations of what a rigorous study looks like, or engage in QRPs. I think that is basically right. It is why I believe that any attempt to reduce QRPs has to be accompanied by changes to incentive structures, which govern the first two.

Peterson also suggests that QRPs are “becoming increasingly unacceptable.” That may be true in public discourse, but the inside view presented by his ethnography suggests that unless more open practices become standard, labs will continue to have lots of opportunity to engage in them and little incentive not to.

UPDATE: I discuss what all this means in a followup post: Reading “The Baby Factory” in context.

A Pottery Barn rule for scientific journals

Proposed: Once a journal has published a study, it becomes responsible for publishing direct replications of that study. Publication is subject to editorial review of technical merit but is not dependent on outcome. Replications shall be published as brief reports in an online supplement, linked from the electronic version of the original.


I wrote about this idea a year ago when JPSP refused to publish a paper that failed to replicate one of Daryl Bem’s notorious ESP studies. I discovered, immediately after writing up the blog post, that other people were thinking along similar lines. Since then I have heard versions of the idea come up here and there. And strands of it came up again in David Funder’s post on replication (“[replication] studies should, ideally, be published in the same journal that promulgated the original, misleading conclusion”) and the comments to it. When a lot of people are coming up with similar solutions to a problem, that’s probably a sign of something.

Like a lot of people, I believe that the key to improving our science is through incentives. You can finger-wag about the importance of replication all you want, but if there is nowhere to publish and no benefit for trying, you are not going to change behavior. To a large extent, the incentives for individual researchers are controlled through institutions — established journal publishers, professional societies, granting agencies, etc. So if you want to change researchers’ behavior, target those institutions.

Hence a Pottery Barn rule for journals: once you publish a study, you own its replicability (or at least a significant piece of it).

This would change the incentive structure for researchers and for journals in a few different ways. For researchers, there are currently insufficient incentives to run replications. This would give them a virtually guaranteed outlet for publishing a replication attempt. Such publications should be clearly marked on people’s CVs as brief replication reports (probably by giving the online supplement its own journal name, e.g., Journal of Personality and Social Psychology: Replication Reports). That would make it easier for the academic marketplace (like hiring and promotion committees, etc.) to reach its own valuation of such work.

I would expect that grad students would be big users of this opportunity. Others have proposed that running replications should be a standard part of graduate training (e.g., see Matt Lieberman’s idea). This would make it worth students’ while, but without the organizational overhead of Matt’s proposal. The best 1-2 combo, for grad students and PIs alike, would be to embed a direct replication in a replicate-and-extend study. Then if the “extend” part does not work out, the replication report is a fallback (hopefully with a footnote about the failed extend). And if it does, the new paper is a more cumulative contribution than the shot-in-the-dark papers we often see now.

A system like this would change the incentive structure for original studies too. Researchers would know that whatever they publish is eventually going to be linked to a list of replication attempts and their outcomes. As David pointed out, knowing that others will try to replicate your work — and in this proposal, knowing that reports of those attempts would be linked from your own paper! — would undermine the incentives to use questionable research practices far better than any heavy-handed regulatory response. (And if that list of replication attempts is empty 5 years down the road because nobody thinks it’s worth their while to replicate your stuff? That might say something too.)

What about the changed incentives for journals? One benefit would be that the increased accountability for individual researchers should lead to better quality submissions for journals that adopted this policy. That should be a big plus.

A Pottery Barn policy would also increase accountability for journals. It would become much easier to document a journal’s track record of replicability, which could become a counterweight to the relentless pursuit of impact factors. Such accountability would mean a greater emphasis on evaluating replicability during the review process — e.g., to consider statistical power, to let reviewers look at the raw data and the materials and stimuli, etc.

But sequestering replication reports into an online supplement means that the journal’s main mission can stay intact. So if a journal wants to continue to focus on groundbreaking first reports in its main section, it can continue to do so without fearing that its brand will be diluted (though I predict that it would have to accept a lower replication rate in exchange for its focus on novelty).

Replication reports would generate some editorial overhead, but not nearly as much as original reports. They could be published based directly on an editorial decision, or perhaps with a single peer reviewer. A structured reporting format like the one used at Psych File Drawer would make it easier to evaluate the replication study relative to the original. (I would add a field to describe the researchers’ technical expertise and experience with the methods, since that is a potential factor in explaining differences in results.)

Of course, journals would need an incentive to adopt the Pottery Barn rule in the first place. Competition from outlets like PLoS One (which does not consider importance/novelty in its review criteria) or Psych File Drawer (which only publishes replications) might push the traditional journals in this direction. But ultimately it is up to us scientists. If we cite replication studies, if we demand and use outlets that publish them, and if we we speak loudly enough — individually or through our professional organizations — I think the publishers will listen.

Replication, period. (A guest post by David Funder)

The following is a guest post by David Funder. David shares some of his thoughts about the best way forward through social psychology’s recent controversies over fraud and corner-cutting. David is a highly accomplished researcher with a lot of experience in the trenches of psychological science. He is also President-Elect of the Society for Personality and Social Psychology (SPSP), the main organization representing academic social psychologists — but he emphasizes that he is not writing on behalf of SPSP or its officers, and the views expressed in this essay are his own.


Can we believe everything (or anything) that social psychological research tells us? Suddenly, the answer to this question seems to be in doubt. The past few months have seen a shocking series of cases of fraud –researchers literally making their data up — by prominent psychologists at prestigious universities. These revelations have catalyzed an increase in concern about a much broader issue, the replicability of results reported by social psychologists. Numerous writers are questioning common research practices such as selectively reporting only studies that “work” and ignoring relevant negative findings that arise over the course of what is euphemistically called “pre-testing,” increasing N’s or deleting subjects from data sets until the desired findings are obtained and, perhaps worst of all, being inhospitable or even hostile to replication research that could, in principle, cure all these ills.

Reaction is visible. The European Association of Personality Psychology recently held a special three-day meeting on the topic, to result in a set of published recommendations for improved research practice, a well-financed conference in Santa Barbara in October will address the “decline effect” (the mysterious tendency of research findings to fade away over time), and the President of the Society for Personality and Social Psychology was recently motivated to post a message to the membership expressing official concern. These are just three reactions that I personally happen to be familiar with; I’ve also heard that other scientific organizations and even agencies of the federal government are looking into this issue, one way or another.

This burst of concern and activity might seem to be unjustified. After all, literally making your data up is a far cry from practices such as pre-testing, selective reporting, or running multiple statistical tests. These practices are even, in many cases, useful and legitimate. So why did they suddenly come under the microscope as a result of cases of data fraud? The common thread seems to be the issue of replication. As I already mentioned, the idealistic model of healthy scientific practice is that replication is a cure for all ills. Conclusions based on fraudulent data will fail to be replicated by independent investigators, and so eventually the truth will out. And, less dramatically, conclusions based on selectively reported data or derived from other forms of quasi-cheating, such as “p-hacking,” will also fade away over time.

The problem is that, in the cases of data fraud, this model visibly and spectacularly failed. The examples that were exposed so dramatically — and led tenured professors to resign from otherwise secure and comfortable positions (note: this NEVER happens except under the most extreme circumstances) — did not come to light because of replication studies. Indeed, anecdotally — which, sadly, seems to be the only way anybody ever hears of replication studies — various researchers had noticed that they weren’t able to repeat the findings that later turned out to be fraudulent, and one of the fakers even had a reputation of generating data that were “too good to be true.” But that’s not what brought them down. Faking of data was only revealed when research collaborators with first-hand knowledge — sometimes students — reported what was going on.

This fact has to make anyone wonder: what other cases are out there? If literal faking of data is only detected when someone you work with gets upset enough to report you, then most faking will never be detected. Just about everybody I know — including the most pessimistic critics of social psychology — believes, or perhaps hopes, that such outright fraud is very rare. But grant that point and the deeper moral of the story still remains: False findings can remain unchallenged in the literature indefinitely.

Here is the bridge to the wider issue of data practices that are not outright fraudulent, but increase the risk of misleading findings making it into the literature. I will repeat: so-called “questionable” data practices are not always wrong (they just need to be questioned). For example, explorations of large, complex (and expensive) data sets deserve and even require multiple analyses to address many different questions, and interesting findings that emerge should be reported. Internal safeguards are possible, such as split-half replications or randomization analyses to assess the probability of capitalizing on chance. But the ultimate safeguard to prevent misleading findings from permanent residence in (what we think is) our corpus of psychological knowledge is independent replication. Until then, you never really know.

Many remedies are being proposed to cure the ills, or alleged ills, of modern social psychology. These include new standards for research practice (e.g., registering hypotheses in advance of data gathering), new ethical safeguards (e.g., requiring collaborators on a study to attest that they have actually seen the data), new rules for making data publicly available, and so forth. All of these proposals are well-intentioned but the specifics of their implementation are debatable, and ultimately raise the specter of over-regulation. Anybody with a grant knows about the reams of paperwork one now must mindlessly sign attesting to everything from the exact percentage of their time each graduate student has worked on your project to the status of your lab as a drug-free workplace. And that’s not even to mention the number of rules — real and imagined — enforced by the typical campus IRB to “protect” subjects from the possible harm they might suffer from filling out a few questionnaires. Are we going to add yet another layer of rules and regulations to the average over-worked, under-funded, and (pre-tenure) insecure researcher? Over-regulation always starts out well-intentioned, but can ultimately do more harm than good.

The real cure-all is replication. The best thing about replication is that it does not rely on researchers doing less (e.g., running fewer statistical tests, only examining pre-registered hypotheses, etc.), but it depends on them doing more. It is sometimes said the best remedy for false speech is more speech. In the same spirit, the best remedy for misleading research is more research.

But this research needs to be able to see the light of day. Current journal practices, especially among our most prestigious journals, discourage and sometimes even prohibit replication studies from publication. Tenure committees value novel research over solid research. Funding agencies are always looking for the next new thing — they are bored with the “same old same old” and give low priority to research that seeks to build on existing findings — much less seeks to replicate them. Even the researchers who find failures to replicate often undervalue them. I must have done something wrong, most conclude, stashing the study into the proverbial “file drawer” as an unpublishable, expensive and sad waste of time. Those researchers who do become convinced that, in fact, an accepted finding is wrong, are unlikely to attempt to publish this conclusion. Instead, the failure becomes fodder for late-night conversations, fueled by beverages at hotel bars during scientific conferences. There, and pretty much only there, can you find out which famous findings are the ones that “everybody knows” can’t be replicated.

I am not arguing that every replication study must be published. Editors have to use their judgment. Pages really are limited (though less so in the arriving age of electronic publishing) and, more importantly, editors have a responsibility to direct the limited attentional resources of the research community to articles that matter. So any replication study should be carefully evaluated for the skill with which it was conducted, the appropriate level of statistical power, and the overall importance of the conclusion. For example, a solid set of high-powered studies showing that a widely accepted and consequential conclusion was dead wrong, would be important in my book. (So would a series of studies confirming that an important surprising and counter-intuitive finding was actually true. But most aren’t, I suspect.) And this series of studies should, ideally, be published in the same journal that promulgated the original, misleading conclusion. As your mother always said, clean up your own mess.

Other writers have recently laid out interesting, ambitious, and complex plans for reforming psychological research, and even have offered visions of a “research utopia.” I am not doing that here. I only seek to convince you of one point: psychology (and probably all of science) needs more replications. Simply not ruling replication studies as inadmissible out-of-hand would be an encouraging start. Do I ask too much?

From Walter Stewart to Uri Simonsohn

Over on G+, Ole Rogeberg asks what ever happened to Walter Stewart? Stewart was a biologist employed by NIH in the 80s and 90s who became involved in rooting out questionable research practices.

Rogeberg posts an old Omni Magazine interview with Stewart (from 1989) in which Stewart describes how he got involved in investigating fraud and misconduct and what led him to think that it was more widespread than many scientists were willing to acknowledge. If you have been following the fraud scandals in psychology and the work of Uri Simonsohn, you should read it. It is completely riveting. And I found some of the parallels to be uncanny.

For example, on Stewart’s first investigation of questionable research, one of the clues that raised his suspicions was a pattern of too-similar means in a researcher’s observations. Similar problems — estimates closer together than what would be expected by chance — led Simonsohn to finger 2 researchers for misconduct.

And anticipating contemporary calls for more data openness — including the title of Simonsohn’s working paper, “Just Post It,” Stewart writes:

“With present attitudes it’s difficult for an outsider to ask for a scientist’s raw data without appearing to question that person’s integrity. But that attitude absolutely has to change… Once you publish a paper, you’re in essence giving its ideas away. In return for benefits you gain from that – fame, recognition, or whatever – you should be willing to make your lab records and data available.”

Some of the details of how Stewart’s colleagues responded are also alarming. His boss at NIH mused publicly on why he was wasting his talents chasing fraud. Others were even less kind, calling him “the terrorist of the lab.” And when he got into a dispute with his suburban neighbors about not mowing his lawn, Science — yes, that Science — ran a gossip piece on the spat. (Some of the discussions of Simonsohn’s earlier data-detecting efforts have gotten a bit heated, but I haven’t seen anything get that far yet. Let’s hope there aren’t any other social psychologists on the board of his HOA.)

The Stewart interview brought home for me just how much these issues are perennial, and perhaps structural. But the difference from 23 years ago is that we have better tools for change. Journal editors’ gatekeeping powers are weakening in the face of open-access journals and post-publication review.

Will things change for the better? I don’t know. I feel like psychology has an opportunity right now. Maybe we’ll actually step back, have a difficult conversation about what really needs to be done, and make some changes. If not, I bet it won’t be 20 years before the next Stewart/Simonsohn comes along.