The Problem With Cultural Evolution

I will now roast myself and my scientific field. This is therapy designed to elicit self-criticism in myself and in my colleagues. The themes are real though. I have heard variations of them from diverse colleagues. This post coincides with this year’s annual Cultural Evolution Society meeting in Aarhus. I hope it incites some animated discussions.

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Cultural Evolution is a growing international and highly interdisciplinary field of scholarship. In the 1980s, there were at most a dozen tenured professors focused on it. Now there is a Cultural Evolution Society, which is well-funded enough to offer its own research grants. Cultural evolution is a common topic in top scientific journals. And there have been several popular science books about it in the last decade. It is also a demographically young field, with junior scholars producing a majority of its output.

The framework of human cultural evolution has become a standard part of any scientific story of human evolution and the dynamics and diversity of human societies. That was not always true—the importance of socially transmitted behavior was routinely downplayed last century. Few fields have enjoyed such rapid and interdisciplinary success.

So what went wrong?

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The field of cultural evolution, like any rapidly growing field, has some pruning to do. Parts of it are an undisciplined bandwagon characterized by vague theorizing or even worse no theorizing at all. I’m looking at you, “cumulative culture.” It is methodologically chaotic, and links between theory and evidence are often more metaphorical than logical. The field enjoys broad scholarly and public interest, and so as a result some of the most prominent cultural evolution research is exaggerated story-telling sinking on a swamp of illogical and opaque data analysis.

We expect all of that from evolutionary psychology. We were supposed to be better.

The field has tremendous potential as a scientific framework for the study of animal and human societies. But it must invest more in self-criticism and rigor, if it is going to do more than produce entertainment for college-educated elites.

There are three major problems.

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First, too many cultural evolution scholars do not know the foundational theory of the field. The field began as the mathematical study of socially transmitted behavior. This kept the field small at first. As the field has grown, the average mathematical sophistication has declined. Not everyone needs to be a theorist. No one wants that. But too many have replaced formal knowledge of theory with gossip about what the models contain or predict. This leads in turn to irrelevant investigations and the reinvention of ideas.

At the first meeting of the Cultural Evolution Society in 2017, I introduced Professor Pete Richerson, one of the founding figures of the field, by saying his 1985 book (with Rob Boyd) is one of the most cited works in cultural evolution but possibly the least read. Everyone laughed. But it wasn’t (only) a joke. Scholarship matters.

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Second, too much empirical work is performative. It is thematically about culturally evolution. But it makes little meaningful connection to theory. Little is learned from an experiment or field study with no theoretical implications. And an experiment or field study motivated by conceptual resemblance rarely has clear implications for our scientific beliefs. Culturally evolutionary phenomena are complex. Rejecting null models of no association between convenient measures of poorly-defined concepts is not a progressive scientific program.

When empirical programs in cultural evolution began, they were closely tied to theoretical implications. However the foundational models are insufficient, because they were highly abstract and usually inapplicable to any precise empirical context. Before meaningful traction between theory and data can be made, new models must be constructed that have the resolution of the data. This is the same awkward evolution that population genetics underwent as it became an empirical science.

Cultural evolution has just begun to recognize the problem. It took me far too long to recognize it myself, and I was supposed to know better.

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Third, most cultural evolution scholars do not understand much about the logical requirements for causal data analysis. Our field is inherently observational. Causal inference is possible in observational settings. But what is needed for a statistical procedure to yield causal insight is always a separate generative model that justifies the statistical procedure. Hierarchical models and model selection have nothing to offer by themselves.

The unavoidable conclusion is that most of the causal claims in the published literature make no sense. Maybe they are correct. But in science, being correct isn’t enough. The conclusion must also be transparently justified. Experiments are not immune to this requirement.

Descriptive work is equally as valuable as inferential work. But it is also equally vulnerable, because scientifically relevant measurement is rarely possible without causal thinking about the nature of measurement and the origin of the sample. There is always missing data, and there is usually sampling bias as well, and causal assumptions are required to justify how accurate descriptions can be derived from such samples.

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I have participated myself in every one of the problems above. For each of them, I could produce specific examples. Each would be highly cited. It’s not the fringes that are flawed. And everyone knows it, unless the only standard of success one cares about is publication and funding.

I could also produce examples of high-quality scholarship in cultural evolution. Such work is often modest, thoroughly documented, and less cited. Let’s do more of that. Let’s commit to training the future of the discipline so that they have the skills needed to realize the discipline’s potential. For senior people, this will usually require admitting that we have to relearn some things ourselves. The published literature is not a pile of facts. It is a record of struggle against a hostile universe.

So what can we do, while treating one another humanely? The simplest thing is to ask one another for clear theoretical estimands. What are we even supposed to be learning from a study? And under which assumptions do the measures and procedures provide it? These are often difficult questions to answer. And all of us need practice answering them but also asking them.

Postscript.

A (minority) reaction to this essay that has surprised me: “But things are worse in others fields.” I don’t care if things are worse in other fields. There are absolute scholarly standards to adhere to. Nature (not the journal, but the universe) isn’t going to cough up insight just because we are better than some branch of social psychology.

Post-postscript.

I’ve offended some evolutionary psychologists with my comment that we “expect all of that from evolutionary psychology”. This was a joke about neighboring fields being competitive. I could have used “cultural anthropology” or “sociology” or “behavioral ecology” instead. But the joke works better with “evolutionary psychology,” because it is widely believed (outside of evolutionary psychology) that evolutionary psychology is a sloppy field with toxic politics. You don’t have to agree to see that comparison with it makes for the most effective way to cut my own field.