I was talking with someone today about various “dead on arrival” research programs we’ve been discussing here for the past few years: I’m talking about topics such beauty and sex ratios of children, or ovulation and voting, or ESP—all of which possibly represent real phenomena and could possibly be studied in a productive way, just not using the data collection and measurement strategies now in use. This is just my opinion, but it’s an opinion based on a mathematical analysis (see full story here) that compares standard errors with plausible population differences
Anyway, my point here is not to get into another argument with Satoshi Kanazawa or Daryl Bem or whoever. They’re doing their research, I’m doing mine, and at this point I don’t think they’re planning to change their methods.
Instead, accept for a moment my premise that these research programs, as implemented, are dead ends. Accept my premise that these researchers are chasing noise, that they’re in the position of the “50 shades of gray” guys but without the self-awareness. They think they’re doing research and making discoveries but they’re just moving in circles.
OK, fine, but then the question arises: what is the role of data and experimental results in these research programs?
Here’s what I think. First, when it comes to the individual research articles, I think the data add nothing, indeed the data can even be a minus if they lead other researchers to conclude that a certain pattern holds in the general population.
From this perspective, if these publications have value, it’s in spite of, not because of, their data. If the theory is valuable (and it could be), then it could (and, I think, should) stand alone. It would be good if the theory also came with quantitative predictions that were consistent with the rest of available scientific understanding, which would in turn motivate a clearer understanding of what can be learned from noisy data in such situations—but let’s set that aside, let’s accept that these people are working within their own research paradigm.
So what is that paradigm? By which I mean, not What is their paradigm of evolutionary psychology or paranormal perception or whatever, but What is their paradigm of how research proceeds? How will their careers end up, and how will these strands of research go forward.
I think (but certainly am not sure) that these scientists think of themselves as operating in Popperian fashion, coming up with scientific theories that imply testable predictions, then designing measurements and experiments to test their hypotheses, rejecting when “p less than .05” and moving forward. Or, to put it slightly more loosely, they believe they are establishing stylized facts, little islands of truth in our sea of ignorance, and jumping from island to island, building a pontoon bridge of knowledge . . . ummmm, you get the picture. The point is, that from their point of view, they’re doing classic science. I don’t think this is what’s happening, though, for reasons I discussed here a few months ago.
But, if these researchers are not following the Karl Popper playbook, what are they doing?
A harsh view, given all I’ve written above, is that they’re just playing in a sandbox with no connection to science or the real world.
But I don’t take this harsh view. I accept that theorizing is an important part of science, and I accept that the theorizing of Daryl Bem, or Sigmund Freud, or the himmicanes and hurricanes people, or the embodied cognition researchers, etc etc etc., is science, even if these researchers do not have a realistic sense of the sort of measurement accuracy it would take to test and evaluate these theories.
Now we’re getting somewhere. What I think is that anecdotes, or case studies, even data that are so noisy as to essentially be random numbers, can be a helpful stimulus, in that it can motivate some theorizing.
Take, for example, that himmicanes and hurricanes study. The data analysis was a joke (no more so than a lot of other published data analyses, of course), and the authors of the paper made a big mistake to double down on their claims rather than accepting the helpful criticism from outside—but maybe there’s something to their idea that the name of a weather event affects how people react to it. It’s quite possible that, if there is such an effect, it goes in the opposite direction from what was claimed in that notorious article—but the point is that their statistical analyses may have jogged them into an interesting theory.
It’s the same way, I suppose, that Freud came up with and refined his theories of human nature, based on his contacts with individual patients. In this case, researchers are looking at individual datasets, but it’s the same general idea.
Anyway, here’s my point. To the extent that research of Bem, or Kanazawa, or the ovulation-and-voting people, or the himmicanes-and-hurricanes people, or whatever, has value, I think the value comes from the theories, not from the data and certainly not from whatever happens to show up as statistically significant in some power=.06 study. And, once we recognize that the value comes in the theories, it suggests that the role of the data is to throw up random numbers that will tickle the imagination of theorists. Even if they don’t realize that’s what they’re doing.
Sociologist Jeremy Freese came up with the term Columbian Inquiry to describe scientists’ search for confirmation of a vague research hypothesis: “Like brave sailors, researchers simply just point their ships at the horizon with a vague hypothesis that there’s eventually land, and perhaps they’ll have the rations and luck to get there, or perhaps not. Of course, after a long time at sea with no land in sight, sailors start to get desperate, but there’s nothing they can do. Researchers, on the other hand, have a lot of more longitude—I mean, latitude—to terraform new land—I mean, publishable results—out of data . . .”
What I’ve attempted to do in the above post is, accepting that a lot of scientists do proceed via Columbian Inquiry, try to understand where this leads. What happens if you spend a 40-year scientific career using low-power studies to find support for, and modify, vague research hypotheses? What will happen is that you’ll move in a sort of directed random walk, finding one thing after another, one interaction after another (recall that we’ve looked at studies that find interactions with respect to relationship status, or weather, or parents’ socioeconomic status—but never in the same paper), but continuing to stay in the main current of your subfield. There will be a sense of progress, and maybe real progress (to the extent that the theories lead to useful insights that extend outside your subfield), even if the data aren’t quite playing the role that you think they are.
For example, Satoshi Kanazawa, despite what he might think, is not discovering anything about variation in the proportion of girl births. But, by spending years thinking of explanations for the patterns in his noisy data, he’s coming up with theory after theory, and this all fits into his big-picture understanding of human nature. Sure, he could do all this without ever seeing data at all—indeed, the data are, in reality, so noisy as to have have no bearing on his theorizing—but the theories could still be valuable.
P.S. I’m making no grand claims for my own research. Much of my political science work falls in a slightly different tradition in which we attempt to identify and resolve “puzzles” or stylized facts that do not fit the current understanding. We do have some theories, I guess—Gary and I talked about “enlightened preferences” in our 1993 paper—but we’re a bit closer to the ground. Also we tend to study large effects with large datasets so I’m not so worried that we’re chasing noise.