Wegner’s article “The Premature Demise of the Solo Experiment” in PSPB (1992) is an interesting document for meta-psychologists. It provides some insight into the thinking of leading social psychologists at the time; not only the author, but reviewers and the editor who found this article worthy of publishing, and numerous colleagues who emailed Wegner with approving comments.
The article starts with the observation that in the 1990s social psychology journals increasingly demanded that articles contain more than one study. Wegner thinks that the preference of multiple-study articles is a bias rather than a preference in favour of stronger evidence.
“it has become evident that a tremendous bias against the “solo” experiment exists that guides both editors and reviewers” (p. 504).
The idea of bias is based on the assumption that rejection a null-hypothesis with a long-run error-probability of 5% is good enough to publish exciting new ideas and give birth to wonderful novel theories. Demanding even just one replication of this finding would create a lot more burden without any novel insights just to lower this probability to 0.25%.
“But let us just think a moment about the demise of the solo experiment. Here we have a case in which skepticism has so overcome the love of ideas that we seem to have squared the probability of error we are willing to allow. Once, p < .05 was enough. Now, however, we must prove things twice. The multiple experiment ethic has surreptitiously changed alpha to .0025 or below.”
That’s right. The move from solo-experiment to multiple-study articles shifted the type-I error probability. Even a pair of studies reduced the type-I error probability more than the highly cited and controversial call to move alpha from .05 to .005. A pair of studies with p < .05 reduces the .005 probability by 50%!
Wegner also explains why journals started demanding multiple studies.
After all, the statistical reasons for multiple experiments are obvious-what better protection of the truth than that each article contain its own replication? (p. 505)
Thus, concerns about replicabilty in social psychology were prominent in the early 1990s, twenty years before the replication crisis. And demanding replication studies was considered to be a solution to this problem. If researchers were able to replicate their findings, ideally with different methods, stimuli, and dependent variables, the results are robust and generalizable. So much for the claim that psychologists did not value or conduct replication studies before the open science movement was born in the early 2010.
Wegner also reports about his experience with attempting to replicate his perfectly good first study.
“Sometimes it works wonderfully….more often than not, however, we find the second
experiment is harder to do than the first…Even if we do the exact same experiment again” (p. 506).
He even cheerfully acknowledge that the first results are difficult to replicate because the first results were obtained with some good fortune.
“Doing it again, we will be less likely to find the same thing even if it is true, because the
error variance regresses our effects to the mean. So we must add more subjects right off the bat. The joy of discovery we felt on bumbling into the first study is soon replaced by the strain of collecting an all new and expanded set of data to fend off the pointers [pointers = method-terrorists]” (p. 506).
Wegner even thinks that publishing these replication studies is pointless because readers expect the replication study to work. Sure, if the first study worked, so will the second.
This is something of a nuisance in light of the reception that our second experiment will likely get Readers who see us replicate our own findings roll their eyes and say “Sure,” and we wonder why we’ve even gone to the trouble.
However, he fails to examine more carefully why a successful replication study receives only a shoulder-shrug from readers. After all, his own experience was that it was quite difficult to get these replication studies to work. Doesn’t this mean readers should be at the edge of their seats and wonder whether the original result was a false positive or whether it can actually be replicated? Isn’t the second study the real confirmatory test where the rubber hits the road? Insiders of course know that this is not the case. The second study works because it would not have been included in the multiple-study article if it hadn’t worked. That is after all how the field operated. Everybody had the same problems to get studies to work that Wegner describes, but many found a way to get enough studies to work to meet the demands of the editor. The number of studies was just a test of the persistence of a researcher, not a test of a theory. And that is what Wegner rightfully criticized. What is the point of producing a set of studies with p < .05, if more studies do not strengthen the evidence for a claim. We might as well publish a single finding and then move on to find more interesting ideas and publish them with p-values less than .05. Even 9 studies with p < .05 don’t mean that people can foresee the future (Bem, 2011), but it is surely an interesting idea.
Wegner also comments on the nature of replication studies that are now known as conceptual replication studies. The justification for conceptual replication studies is that they address limitations that are unavoidable in a single study. For example, including a manipulation check may introduce biases, but without one, it is not clear whether a manipulation worked. So, ideally the effect could be demonstrated with and without a manipulation check. However, this is not how conceptual replication studies are conducted.
We must engage in a very delicate “tuning” process to dial in a second experiment that is both sufficiently distant from and sufficiently similar to the original. This tuning requires a whole set of considerations and skills that have nothing to do with conducting an experiment. We are not trained in multi experiment design, only experimental design, and this enterprise is therefore largely one of imitation, inspiration, and luck.
So, to replicate original results that were obtained with a healthy dose of luck, more luck is needed in finding a condition that works, or simply to try often enough until luck strikes again.
Given the negative attitude towards rigor, Wegner and colleagues also used a number of tricks to make replication studies work.
“Some of us use tricks to disguise our solos. We run “two experiments” in the same session with the same subjects and write them up separately. Or we run what should rightfully be one experiment as several parts, analyzing each separately and writing it up in bite-sized pieces as a multi experiment Many times, we even hobble the first experiment as a way of making sure there will be something useful to do when we run another.” (p. 506).
If you think this sounds like some charlatans who enjoy pretending to be scientists, your impression is rather accurate because the past decade has shown that many of these internal replications in multiple study articles were obtained with tricks and provide no empirical test of empirical hypotheses; p-values are just for show so that it looks like science, but it isn’t.
My own views on this issue are that the multiple study format was a bad fix for a real problem. The real problem was that it was all to easy to get p < .05 in a single study to make grand claims about the causes of human behavior. Multiple-study articles didn’t solve this problem because researchers found ways to get significant results again and again even when their claims were false.
The failure of multiple-study articles to fix psychology has some interesting lessons for the current attempts to improve psychology. Badges for data sharing and preregistration will not improve psychology, if they are being gamed like psychologists gamed the multiple-study format. Ultimately, science can only advance if results are reported honestly and if results are finally able to falsify theoretical predictions. Psychology will only become a science when brilliant novel ideas can be proven false and scientific rigor is prized as much as the creation of interesting ideas. Coming up with interesting ideas is philosophy. Psychology emerged as a distinct discipline in order to subject those theories to empirical tests. After a century of pretending to do so, it is high time to do so for real.
3 thoughts on “The Demise of the Solo Experiment”
Fascinating read. The only part I disagree with is the second part of this sentence: “Everybody had the same problems to get studies to work that Wagner describes, but everybody found a way to get enough studies to work to meet the demands of the editor.”
In fact, lots of people didn’t have the persistence, luck (or as R Index would probably say) “flair” to come up with successful follow-up studies.Some were friends/acquaintances of mine. They ended up under-employed or unemployed. This could have included me, if I hadn’t switched from experimental social psychology to personality in the nick of time.
the curse of overgeneralizing to make it more interesting. Will correct this asap.