In my previous post, I wrote about my views on some proposed changes in scientific practice to increase reproducibility. Much has been made of preregistration, publication of null results, and Bayesian statistics as important changes to how we do business. But my view is that there is relatively little value in appending these modifications to a scientific practice that is still about one-off findings; and applying them mechanistically to a more careful, cumulative practice is likely to be more of a hindrance than a help. So what do we do? Here are the modifications to practice that I advocate (and try to follow myself).
1. Cumulative study sets with internal replication.
If I had to advocate for a single change to practice, this would be it. In my lab we never do just one study on a topic, unless there are major constraints of cost or scale that prohibit that second study. Because one study is never decisive.* Build your argument cumulatively, using the same paradigm, and include replications of the key effect along with negative controls. This cumulative construction provides "pre-registration" of analyses – you need to keep your analytic approach and exclusion criteria constant across studies. It also gives you a good intuitive estimate of the variability of your effect across samples. The only problem is that it's harder and slower than running one-off studies. Tough. The resulting quality is orders of magnitude higher.
If you show me a one-off study and I fail to replicate it in my lab, I will tend to suspect that you got lucky or p-hacked your way to a result. But if you show me a package of studies with four internal replications of an effect, I will believe that you know how to get that effect – and if I don't get it, I'll think that I'm doing something wrong.
2. Everything open by default.
There is a huge psychological effect to doing all your work knowing that everyone will see all your data, your experimental stimuli, and your analyses. When you're tempted to write sloppy, uncommented code, you think twice. Unprincipled exclusions look even more unprincipled when you have to justify each line of your analysis.** And there are incredible benefits of releasing raw stimuli and data – reanalysis, reuse, and error checking. It can make you feel very exposed to have all your experimental data subject to reanalysis by reviewers or random trolls on the internet. But if there is an obvious, justifiable reanalysis that A) you didn't catch and B) provides evidence against your interpretation, you should be very grateful if someone finds it (and even more so if it's before publication).
3. Larger N.
4. Better visualizations of variability.
If you run a lot of studies, show all of their results together in one big plot. And show us the variability of those measurements in a way that allows us to understand how much precision you have. Then we will know whether you really have evidence that you understand and whether you can consistently predict either the existence or the magnitude of an effect. Use 95% CIs or Bayesian credible intervals or HPD intervals or whatever strikes your fancy. Frequentist CIs do perform badly when you have just a handful of datapoints, but they do fine when N is large (see above). But come on: this one is obvious: Standard error of the mean is a terrible guide to inference. I care much less about frequentist or Bayesian and much, much more about whether it's 95% vs. 68%.
5. Manipulation checks, positive controls, and negative controls.The reproducibility project was a huge success, and I'm very proud to have been part of it. But I felt that one intuition about replicability was missing from the assessment of the results: whether the experimenters thought they could have "fixed" the experiment. Meaning, there are some findings that when they fail to replication, you have no recourse – you have no idea what to do next. The original paper found a significant effect and a decent effect size, you find nothing. But there are other experiments where you know what happened, based on the pattern of results: the manipulation failed, or the population was different, or the baseline didn't work. In these studies, you typically know what to do next – strengthen the manipulation, alter the stimuli for the population, modify the baseline.
The paradigms you can "debug" – repeat iteratively to adjust them for your situation or population – typically have a number of internal controls. These usually include manipulation checks, positive controls, or negative controls (sometimes even all three). Manipulation checks tell you that the manipulation had the desired effect – e.g., if you are inducing people to identify with a particular group, they actually do, or if you are putting people under cognitive load they are actually under load. Negative controls show that in the absence of the manipulation there is no difference in the measure – they are a sanity check that other aspects of the experimental situation are not causing your effect. Positive controls tell you that some manipulation can cause a difference in your measure, hence it is a sensitive measure, even if the manipulation of interest fails. The output of these checks can provide a wealth of information about a failure to replicate and can lead to later successes.
6. Predictions from (quantitative) theory.If all of our theories are vague, verbal one-offs then they provide very little constraint on our empirical measures. That's a terrible situation to be in as a scientist. If we can create quantitative theories that make empirical predictions, then these theories provide strong constraints on our data – if we don't observe a predicted pattern, we need to rethink either the model or the experiment. While neither one is guaranteed to be right, the theory provides an extra check on the data. I wrote more about this idea here.
7. A broader portfolio of publication outlets.If every manipulation psychologists conducted were important, then we'd want to preregister and publish all of our findings. This situation is – arguably – the case in biomedicine. Every trial is a critical part of the overall outlook on a given drug, and most trials are expensive and risky, so they require regulation and care. But, like it or not, experimental psychology is different. Our work is cheap and typically poses little risk to participants, and there are an infinity of possible psychological manipulations that don't do anything and may never be of any importance.
So, as I've been arguing in previous posts, I think it's silly to advocate that psychologists publish all of their (null) results. There are plenty of reasons not to publish a null result: boringness, bad design, evidence of experimenter error, etc. Of course, there are some null results that are theoretically important and in those cases, we absolutely should publish. But my own research would grind to a halt if I had to write up all the dumb and unimportant things that I've pursued and dropped in the past few years.***
What we need is a broader set of publication outlets that allow us to publish all of the following: exciting new breakthroughs; theoretically deep, complex study sets; general incremental findings; run-of-the-mill replications; and messy, boring, or null results. No one journal can be the right home for all of these. In my view, there's a place for Science and Nature – or some idealized, academically-edited, open-access version of them. I love reading and writing short, broad, exciting reports of the best work on a topic. But there's also a place for journals where the standard is correctness and the reports can include whatever level of detail is necessary to document messy, boring, or null findings that nevertheless will be useful to others going forward. Think PLoS ONE, perhaps without the high article publication charge. The broader point is that we need a robust ecosystem of publication outlets – from high-profile to run-of-the-mill – and some of these outlets need to allow for publication of null results. But whether we publish in them should be a matter of our own scientific responsibility.
A theme running throughout all these recommendations is that I generally believe in all of the principles advocated by folks who want prereg, publication of nulls, and Bayesian data analysis. But their suggestions are almost always posed as mechanical rules: rules that you can follow and know that you are doing science the right way. But these rules should be tempered by our judgment. Preregister if you think that previous work doesn't sufficiently constrain analysis. Publish nulls if they are theoretically important. Use Bayesian tools if they afford some analytic advantages relative to their complexity. But don't do these things just because someone said to. Do them because – in your best scientific judgment – they improve the reliability and validity of the argument you are making.
Thanks to Chris Potts for valuable discussion. Typos corrected afternoon 8/31.
* And, I don't know about you, but when I can only do one study, I always get it wrong.
** I especially like this one: data <- data[data$subid != "S011",]. Damn you, subject 11.
*** I also can't think of anything more boring than reading Studies 1 – 14 in my paper titled "A crazy idea about word learning that never really should have worked anyway and, in the end, despite a false positive in Study 3, didn't amount to anything."
Really nice posts!ReplyDelete
That's a really good post! I have myself been arguing for point 5 (and also 6) for quite some time. Regarding point 4, using CIs (or more robust estimates or perhaps posterior distributions) instead of SEM I also completely - however, I think there is still a lot of resistance to overcome. I've heard of more than one case where reviewers argued effects weren't "significant" or otherwise uninteresting because they interpreted 95%CIs as SEMs. This is something more exposure and education can remedy in the long run but in the short run it isn't helping people get their research published - so unless we find ways to deal with it in the short run too it will never be adopted ;)ReplyDelete
Michael, nice series of posts on this. I think your commentary on Bayesian stats is generally fair. It *is* hard for people to just totally switch to something new after using one set of methods for years and years! Luckily there are parallel tests that have been (are being) developed, that could make the transition easier. Perhaps a way to ease into it is just to report the two types of tests side by side when available. That way people can build an intuition into what the models/tests mean and see where they agree/disagree.ReplyDelete
When a result is significant, the two tests are often in agreement. The more interesting cases are when p-values are not significant, since classical stats can't do much with that!
Anyway, I really really liked you section 6 of this post. I think making the transition to thinking about the quantitative predictions our theories make will be a huge step for psychologists. How can we evaluate a theory if we don't know what to expect when it holds? Prediction is essential.
(Just to plug bayes here: Once we take that leap, it's really only another small step to formally incorporate that information in a bayesian model. I mean, really, researchers are already using some complicated classical modeling techniques. Bayes isn't more complicated, it's just a little different.)
I have been thinking more about your post. You know what else slowing down and being careful would accomplish? It would emphasize quality, strengthen findings, and make it more probable that women get into science and feel like they can succeed and have a family. Data are showing that women are opting out because of the frenzied expectations and the concern that they cannot take time to have families and succeed in this fast and furious environment. A scientific community that is less-frenzied and less dependent on 10 flashy 'surprising' papers per year, and more dependent on quality contributions, may be more attractive in general.ReplyDelete
Dima, I completely agree. Quantity is a bad indicator of scientific quality. But my position is that more people know this than we think. When search committees evaluate applicants, they do look at CV length, but in my experience, they also look for careful and rigorous science. Yet when we *think* about search committees, we imagine the worst case scenario of them just weighing our CVs and perhaps multiplying by journal impact factor. I think there's actually some interesting psychology going on here - it's easy to imagine the counterfactual version of ourselves where we publish more, but it's hard to imagine the counterfactual version of ourselves where we publish work of fundamentally different quality.Delete