Discussions about p-hacking sometimes go sideways. A hypothetical exchange might go like this:
READER: Those p-values are all hovering just below .05, I bet the authors p-hacked.
AUTHOR: I know that I did not p-hack, and I resent the accusation.
By comparison, consider how we talk about another form of potential bias: experimenter effects.
It is widely accepted that experimenters’ expectations, beliefs, or other characteristics can influence participants in behavioral experiments and medical trials. We also accept that this can happen without intent or even awareness on the part of the experimenter. Expectations about how participants receiving a treatment are supposed to differ from those receiving a placebo might show up in the experimenter’s behavior in subtle ways that could influence the participants.
We also don’t have a complete theory of experimenter effects that allows us to reliably measure every manifestation or predict with high confidence when they will and won’t occur. So instead, we consider them as an open possibility in a wide range of situations. As a result, it is also widely accepted that using procedural safeguards against experimenter effects is a best practice in most experiments where a human experimenter will interact with subjects.
Because of all these shared assumptions, discussions around experimenter effects are often much less heated. If you are presenting a study design at lab meeting, and someone says “you’ll need to keep your RAs blind to condition, here’s an idea how to do that…” that’s generally considered a helpful suggestion rather than an insinuation of planned malfeasance.
And even after a study is done, it is generally considered fair game to ask about blinding and other safeguards, and incorporate their presence or absence into an evaluation of a study. If a study lacks such safeguards, authors generally don’t say things like “I would never stoop so low as to try to influence my participants, how dare you!” Everybody, including authors, understands that experimenters don’t always know how they might be influencing subjects. And when safeguards are missing, readers typically treat it as a reason for doubt and uncertainty. We allow and even expect readers to calibrate that uncertainty judgment based on other assumptions or information, like how plausible the effect seems, how strong or weak did partial or incomplete safeguards seem, etc.
For some reason though, when it comes to potential sources of bias in data analysis, we have not (yet) reached a place where we can talk about it in a similar way. This is despite the fact that it has a lot in common with experimenter effects.
It is certainly possible for somebody to deliberately and strategically p-hack, just like it’s possible for an experimenter to wink and nudge and say “are you sure you’re not feeling better?” or whatever. But bias in data analysis does not have to happen that way. Analysts do not have to have intention or even awareness in order to do things that capitalize on chance.
Consider, first of all, that almost every data analysis involves many decisions: what data to include or exclude, whether or how to transform it, a zillion possibilities in specifying the analysis (what particular variables to look at, what analyses to run on them, whether to use one- or two-tailed tests, what covariates to include, which main, interactive, simple, or contrast effect[s] to treat as critical tests of the hypothesis, etc.), and then decisions about what to report. We psychologists of all people know that you cannot un-know something. So once the analyst has seen anything about the data – distributions, scatterplots, preliminary or interim analyses, whatever else – all the subsequent decisions will be made by a person who has that knowledge. And after that point, it is simply impossible for anybody – including the analyst – to state with any confidence how those decisions might otherwise have been made without that knowledge. Which means that we have to treat seriously the possibility that the analyst made decisions that overfit the analyses to the data.
More subtly, as Gelman and Loken discuss in their “forking paths” paper, bias is not defined by a behavior (how many analyses did you run?), but by a set of counterfactuals (how many analyses could you have run?). So even if the objective history is that one and only one analysis was run, that is not a guarantee of no bias.
What all of this means is that when it comes to bias in data analysis, we are in very much a similar situation as with experimenter effects. It is virtually impossible to measure or observe it happening in a single instance, even by the person doing the data analysis. But what we can do is define a broad set of circumstances where we have to take it seriously as a possibility.
It would be great if we could collectively shift our conversations around this issue. I think that would involve changes from both critical readers and from authors.
Start by considering procedures, not behavior or outcomes. Were safeguards in place, and if so, how effective were they? For bias in data analysis, the most common safeguard is preregistration. The mere existence of a preregistration (as indicated by a badge or an OSF link in a manuscript) tells you very little though – many of them do not actually constrain bias. Sometimes that is even by design (for example, preregistering an exploratory study is a great way to prevent editors or reviewers from pressuring you to HARK later on). A preregistration is just a transparency step, you have to actually read it to find out what it does. In order for a preregistration to prevent analytic bias, it has to do two things. First, it has to have a decision inventory – that is, it has to identify all of the decisions about what data to collect/analyze, how to analyze it, and what to report. So ask yourself: is there a section on exclusions? Transformations? Does it say what the critical test is? Etc. (This will be easier to do in domains where you are familiar with the analytic workflow for the research area. It can also be aided by consulting templates. And if authors write and post analysis code as part of a preregistration, that can make things clear too.) Second, the preregistration has to have a plan for all of those decision points. To the extent that the inventory is complete and the plans are specific and were determined separate from the data, the preregistration can be an effective safeguard against bias.
When safeguards are missing or incomplete, everyone – authors and readers alike -should treat analytic bias as a serious possibility. If there is no preregistration or other safeguards, then bias is possible. If there is a preregistration but it was vague or incomplete, bias is also possible. In a single instance it is often impossible to know what actually happened, for the reasons I discussed above. It can be reasonable to start looking at indirect stuff like statistical evidence (like the distribution of p-values), whether the result is a priori implausible, etc. Inferences about these things should be made with calibrated uncertainty. p-curves are neither perfect nor useless; improbable things really do happen though by definition rarely; etc. So usually we should not be too sure in any direction.
Inferences about authors should be rare. We should have a low bar for talking about science and a high bar for talking about scientists. This cuts both ways. Casual talk challenging authors’ competence, intentions, unreported behaviors, etc. is often both hurtful and unjustified when we are talking about single papers.* But also, authors’ positive assertions about their character, behavior, etc. rarely shed light and can have the perverse effect of reinforcing the message that they, and not just the work, are a legitimate part of the conversation. As much as possible, make all the nouns in your discussion things like “the results,” “the procedure,” etc. and not “the authors” (or for that matter “my critics”). And whether you are an author, a critic, or even an observer, you can point out when people are talking about authors and redirect the conversation to the work.
I realize this last item draws a razor-thin line and maybe sometimes it is no line at all. After all, things like what safeguards were in place, and what happened if they weren’t, are results of the researcher’s behavior. So even valid criticism implicates what the authors did or didn’t do, and it will likely be personally uncomfortable for them. But it’s a distinction that’s worth observing as much as you can when you criticize work or respond to criticisms. And I would hope we’ve learned from the ways we talk about experimenter effects that it is possible to have less heated, and frankly more substantive, discussions about bias when we do that.
Finally, it is worth pointing out that preregistration and other safeguards are still really new to psychology and many other scientific fields. We are all still learning, collectively, how to do them well. That means that we need to be able to criticize them openly, publicly, and vigorously – if we do not talk about them, we cannot get better at doing them. But it also means that some preregistration is almost always better than none, because even a flawed or incomplete one will increase transparency and make it possible to criticize work more effectively. Even as we critique preregistrations that could have been done better, we should recognize that anybody who makes that critique and improvement possible has done something of value.
* In the bigger picture, for better or worse, science pins career advancement, resources, prestige, etc. to people’s reputations. So at some point we have to be able to talk about these things. This is a difficult topic and not something I want to get into here, other than to say that discussions about who is a good scientist are probably better left to entirely separate conversations from ones where we scientifically evaluate single papers, because the evidentiary standards and consequences are so different.