One of the things this blog is known for is calling for the death of zombie ideas–ideas that should be dead, but aren’t. Here, “death” basically means “no longer basing any research on the idea.”
Here are two common ways (among many others) in which some readers have pushed back against those posts:
- You have a point, but you’re throwing the baby out with the bathwater. Yes, idea X is a zombie idea–but idea X is only a part of some broader topic on which we need further research. In calling for researchers to abandon idea X, you risk them abandoning worthwhile research on the broader topic. For instance, this is part of Doug Sheil and David Burslem’s response to my critiques of zombie ideas about the intermediate disturbance hypothesis.
- You have a point, but abandoning an entire line of research is too radical a solution. What if you’re wrong about idea X being a zombie? Abandoning an established, ongoing line of research is really risky–what if we’re giving up too soon? Science is hard and it’s normal for a research program to run into obstacles. The only way to make progress is to try as hard as we can to overcome them, not to give up as soon as we encounter them. Brian’s made this argument before.
Both responses highlight the downside risks of abandoning a line of research. And it’s absolutely correct to consider those risks. But of course, just saying “there are downside risks” isn’t enough to determine a course of action, because all courses of action have their own downside risks (and their own upsides). For instance, while we don’t want to throw the baby out with the bathwater, we do want to throw out the bathwater. And while there’s always the risk of giving up on any line of research too soon, there are also risks of giving up too late (e.g., because time, money, and effort spent on a lost cause would be better spent elsewhere).
These are difficult judgement calls to make, and so there will always be disagreement about them.* One way to make these sorts of judgement calls is by drawing on our background knowledge of other similar cases. We’ve talked a lot on this blog about zombie ideas, ideas that should be dead but aren’t. But what about the opposite kind of case? That is:
Has any line of ecological or evolutionary research ever been prematurely abandoned due to criticism from those not pursuing it?
Prematurely abandoned lines of research are the flip side of zombie ideas. They’re dead ideas that should be alive. Ideas that, tragically, left us too soon. I propose calling such ideas Buddy Holly ideas. 🙂 (UPDATE: by “prematurely abandoned”, I mean a line of research that was widely pursued but was abandoned prematurely due to external criticism, analogous to how Buddy Holly became popular but then died in a plane crash. I don’t mean lines of research that were never widely pursued in the first place, even if in retrospect they should’ve been. Such lines of research are more like a singer who never gets discovered.)
Of course, in order to make a strong case that an idea really was prematurely abandoned, it probably needs to be an idea that was later taken up again, successfully. Because unlike Buddy Holly, scientific ideas never perish totally by accident, but always for some reason. So you need to make the case that, even though an idea died for a reason, it wasn’t a good reason.
Note as well that, in order for the subsequent revival of an idea to count as evidence that it’s “death” was premature, the idea needs to be revived in something close to its original form. For instance, while modern research on non-genetic mechanisms of inheritance (maternal effects, DNA methylation, etc.) sometimes is called “Lamarckian”, I think the connections between this modern work and Lamarck’s ideas are far too loose and vague to say that Lamarckianism was prematurely abandoned only to be subsequently revived. Similarly, I think it’s a stretch to call modern evolutionary developmental biology a revival of 19th century German idealist biology (“bauplan” and all that). After all, basically any line of scientific research is going to have some historical antecedent. I mean, there were people who thought that Charles Darwin got his ideas from his grandfather, or from Buffon, or whatever! I’m talking about something much more specific than that.
In an old post I suggested Darwin’s theory of evolution as a possible example of a Buddy Holly idea, since it was “eclipsed” in the late 19th century only to be subsequently revived. Although one can argue about how good an example it is.
Probably the best example of a Buddy Holly idea I can think of is group selection getting abandoned in the late 1960s and ’70s in the wake of criticisms from folks like G. C. Williams and John Maynard Smith, and then revived by folks like David Sloan Wilson. You could interpret the history here as a case of throwing the baby out with the bathwater. Abandoning not only naive, good-of-the-species thinking that really did need to be abandoned, but also viable group selectionist ideas. But I’m not an expert on the history here (which in any case tends to be read differently by different people, I think), so perhaps others can comment.
Perhaps research on food web topology might be an example of a Buddy Holly idea, but I don’t think so. Briefly, back in 1977 Joel Cohen had the creative idea to think of food webs as mathematical objects called graphs (aka networks), with species as “nodes” and predator-prey relationships as “links” connecting predator nodes to prey nodes. Food web data compiled from the literature suggested some surprising general properties of these graphs–for instance, they tended to be “interval”, and the ratio of links to species seemed to be constant (Cohen 1989). And Cohen and others developed simple models to try to explain these apparent patterns. However, the data were of low quality, leading Gary Polis and others to argue powerfully that food web theory was a house built on sand (Polis 1991). But the obvious response to this critique (indeed, the response recommended by Polis himself) was not to abandon this line of research, but to go out and collect better data on who eats whom. Which a lot of people did. Explaining the new patterns in those data subsequently motivated a whole new generation of food web topology models (e.g., Williams and Martinez 2000). So rather than seeing this as a line of research that was prematurely abandoned and then subsequently taken up again, I’d see it as a line of research that only remained productive by taking well-founded criticisms to heart.**
Maybe “randomized null models of species x site matrices as a tool for inferring competition” might be an example of a Buddy Holly idea? Depending on whether you think the revival of interest in that approach since the mid-90s has been productive, or whether you think this approach still is open to some of the same fundamental objections that were raised against it in the late ’70s and early ’80s (I basically take the latter view, but your mileage may vary).
In summary, it looks to me like Buddy Holly ideas are pretty rare, and rarer than zombie ideas. Once a critical mass of researchers decide to pursue an idea, they hardly ever give up on it too soon. Which suggests to me that we don’t really need to worry much that debate and mutual criticism will lead to productive lines of research being abandoned. But what do you think? Are there “Buddy Holly ideas”? Lots of them? Looking forward to your comments.
*If you want to argue that no line of research pursued by professional scientists is ever so unproductive as to merit abandonment, well, ok I guess. But that means you’re ok with not calling for the abandonment of research on ESP, Bigfoot, and tabletop cold fusion, never mind more debatable cases. Or I guess you could say that some lines of research should be abandoned, but that other scientists shouldn’t say so publicly–that it’s best to just publicly ignore lines of research you don’t like. If you can’t say something nice, don’t say anything at all, as the saying goes. Which again, ok I guess. It’s fine if some folks adopt that as their own personal policy. And perhaps in some circumstances it’s the most effective way to encourage abandonment of unproductive lines of research. But personally I’m a little uncomfortable with any argument that says scientists should remain publicly silent about their scientific views, or should never publicly criticize one another’s scientific views. I’m actually not sure if anyone holds such extreme “anti-criticism” views, so I might be addressing a bit of a straw man here. But I’m a believer in thinking through extreme limiting cases, even if they never actually occur in the real world. 🙂
**It probably helped that the criticisms could be addressed in a straightforward fashion. By “straightforward” I don’t mean the criticisms could be addressed easily–collecting diet data for dozens of species in a community is not easy! Rather, I mean it was obvious what sort of new data were needed, and how to obtain them (it was just a lot of work to obtain them). So that addressing the criticisms appeared to many as a really good research opportunity. Criticisms of early observational studies of biodiversity-ecosystem function relationships as confounded by sampling effects were seen in much the same way, I think. People quickly realized how to address the criticisms with new experimental designs and statistical analyses, and so addressing them was seen as a research opportunity. In contrast, when I suggest (as I did at the end of Fox 2012) that the time is ripe for a new generation of work on disturbance-diversity relationships, grounded in modern coexistence theory, it’s not immediately obvious exactly what sort of work that would involve. “Go out and test for storage effects and relative nonlinearity, and see how their strength varies as a function of disturbance frequency and intensity” isn’t straightforward in the way that “go out and assess the diets of every species in a community” is. Or at least, it probably doesn’t seem that way to most people. Put slightly differently, I suspect that calls from Gary Polis and others for better food web data, or calls to address the issue of sampling effects in BD-EF research, sounded to many people like calls to continue the same research programs by different means. While I suspect my call for research on disturbance-diversity relationships to be based on modern coexistence theory rather than the IDH probably sounds to a lot of people like an attempt to change the question, and thus to replace an existing research program with a new (and not clearly-defined) one. Or perhaps I’m wrong, perhaps it’s only with the benefit of hindsight (and perhaps only to my eyes?) that the history of food web research looks like a single continuous research program with a healthy back-and-forth between theory and data? Perhaps at the time, and to those involved, the critiques of Polis and others felt like calls to replace one (in their view failed) research program with an alternative program? I don’t know, just speculating here, comments welcome.