As we’ve discussed several times (e.g., this comment thread), ecologists as a whole may be increasingly skeptical of the value in “pure theory”, meaning theory that is at best only loosely connected to “reality” or “nature”. The evidence for that is anecdotal, but for the sake of discussion let’s assume it’s a real trend. What’s driving it?
In the past, I’ve diagnosed it as an empirical/theoretical divide, arising because empiricists and theoreticians have different motivations and backgrounds (see here, here, here and here, for instance). Or perhaps it’s because technical advances in statistics and software have made it easier to link models and data, so maybe data-linked modeling is crowding out pure theory. But lately I’m wondering if there’s something else to it as well. After all, Brian’s hardly a math phobe, and would never insist on doing science one way rather than another, and yet even he writes:
But as a prescription, models ultimately do need some smash against reality (even the “toy” or strategic models like May advocated)…If they never smash against reality, then I would have to agree they’re not advancing science.
And while Brian has a broad understanding of the phrase “some smash against reality” (taking it to mean much more than just, e.g., having parameters that can be estimated from data), I still think his view contrasts with that of Hal Caswell (1988):
Perhaps the greatest obstacle to understanding the role of theory is the failure to recognize that theoretical studies attempt to solve theoretical problems, and that these problems are a legitimate part of ecology.
Theoretical problems are those arising from a body of theory (or sometimes from the lack of one). One important theoretical problem is: ‘It this theory really true in nature?” (Are more complex ecosystems really more stable?) This problem cannot be solved by theory alone; it requires experimental or observational tests of the predictions of the theory, and the answer is always fallible. However, other, equally important theoretical problems arise any time a theory begins to develop. Some of these problems ask questions about the theory itself; they cannot be answered by empirical investigation.
Caswell’s examples of “theoretical problems” (what I call “pure theory”) include exploring the consequences of alternative assumptions, demonstrating connections between apparently-unrelated theories, and identifying the simplest possible assumptions capable of producing specified results. He was responding to an earlier paper by Dan Simberloff in which Simberloff criticized theory “as remote from biology as faith-healing.” But Caswell could equally well have been responding to others. For instance, back in 1934 Nicolas Tesla wrote,
Today’s scientists have substituted mathematics for experiments, and they wander off through equation after equation, and eventually build a structure which has no relation to reality.
Even theoretical ecologists sometimes express the same worry. Here’s Simon Levin writing in 2012:
The legacy of Volterra and Lotka has not been universally positive, although this is certainly not their fault. The attractive simplicity of the model equations proved irresistible to mathematicians eager to add bells and whistles, with little concern for biological relevance, and to explore their tortured implications in painful detail. This has produced a large literature, harmless except for its effect on perceptions of the field of mathematical biology, and its obfuscation of the cryptic nuggets that sometimes lie within.
I have a hypothesis as to the worry behind comments like Brian’s, Simberloff’s, Tesla’s, or Levin’s. The worry is that, to the extent that theory is unconnected to nature, we have no externally-imposed criteria by which to judge its merits. So doing theory–deciding which theoretical problems are most important or interesting, which approaches are most fruitful, etc.–just becomes a matter of following conventions. And those conventions are arbitrary, intrinsically no better or worse than any other conventions we might have chosen instead. Or worse, maybe there aren’t even any conventions, maybe it’s just anything goes–assume whatever you want (doesn’t matter what, or why), and see what follows. Pure theory on this view is a sort of pointless, free-floating activity, valuable only to its practitioners, and only because they happen to enjoy it. It’s not (just) that it’s remote from biology. It’s remote from anything besides itself.
This is an understandable worry about “pure” theory. It certainly is possible for a collective activity to devolve into pointless navel-gazing, or at least mere games-playing, if it doesn’t have to obey any rules and goals except those that its participants arbitrarily decide to impose. Think of Calvinball, or more broadly any hobby, game, or sport.*
But this is a worry about any human activity, not just theoretical ecology, isn’t it? Conventions and criteria for pretty much anything humans do ultimately are human constructs, at least in large part, aren’t they? For instance, even if you’re doing “purely” empirical research the identity of the interesting and important questions isn’t God-given. Heck, it’s not even something we all agree on. We always have to make judgment calls about what questions to ask and how to answer them, on grounds that others can appreciate if not necessarily agree with.
For instance, probably many birders and ornithologists would say that Mallards are boring birds. They’re everywhere, and they look the same everywhere. But as Andrew Hendry points out, doesn’t that actually make them rather unusual and interesting? That is, the common judgement that Mallards are boring is just that–a judgement. It’s not totally arbitrary–there are understandable reasons for thinking Mallards are boring. But nor is the boringness of Mallards some purely objective external fact that we discovered. Or think of the infamous difficulty of justifying any fundamental research, and distinguishing good fundamental research from mere self-indulgence by smart people with obscure interests. To my eyes, debates within fundamental empirical ecology about what questions or approaches are most worth pursuing don’t look all that much different than, say, debates within pure mathematics as to what branches of mathematics are most worth pursuing.
Yes, it’s possible for pure theory to devolve into pointless study of equations nobody has any good reason to care about. But I think any human activity runs that same risk. So I don’t know that “pure theory” should be singled out for concern here.
What do you think? Looking forward to your comments.**
*Warning: long footnote in which I makes superficial analogies to lots of stuff that is not ecology. It’s quite possibly the most “Jeremy” footnote ever:
It’s perhaps worth noting that analogous worries crop up in all sorts of areas. Many human activities have been argued to become pointlessly self-referential if they’re unmoored from any external criteria of merit. Philosopher Dan Dennett once advised philosophy grad students to avoid studying “artificial puzzles” of no true significance just because they’d been studied by other philosophers. Modern art has been thought pointless because it’s hard to identify agreed-upon external aesthetic criteria by which to evaluate it. A lack of external criteria of merit seems to imply that merit is purely subjective (think of Duke Ellington’s famous remark about how to identify good music: “If it sounds good, it is good“). Closer to home, when you worry about bandwagons in science, you’re worrying that scientists are deciding to pursue research program X just because everyone else is too. Rather than scientists choosing what to work on based on putatively “external” criteria like what’s interesting or important, they’re choosing based on an “internal” or self-referential criterion, namely what other scientists are working on. It’s similar to worries about what happens when people start substituting an index or symptom of something for the thing itself. For instance, judging a movie by how much money it makes, which can lead to studios trying to make movies that will make money rather than making good movies. Or think of picking stocks by just copying the choices of other investors, which leads to market bubbles and crashes if enough people do it, and which would render the stock market non-functional if everyone did it. It’s often argued that politics goes off the rails when politicians start seeking power as an end in itself rather than as a means to the end of achieving some substantive policy goal. But on the other hand, just because an activity operates (or appears to operate) according to “internal” or “self-referential” conventions and criteria doesn’t necessarily mean it’s pointless. Mathematics has sometimes been criticized (or praised) as a useless human invention. We just specify arbitrary axioms, and then derive their consequences. Think of Kronecker’s claim that “God made the integers, all else is the work of man.” But I don’t think those criticisms of mathematics hold much water (if only because even the most seemingly-pointless bits of math keep turning out to be useful; think of how number theory turned out to be essential to cryptography). Or think of the common law, where the law is defined recursively, i.e. via precedent rather than by legislation. So I don’t think you can show that pure ecological theory is pointless merely by pointing to its focus on theoretical problems.
**Because I might be totally off base here. Indeed, I predict that the first comment will be “Sorry Jeremy, but what the hell are you talking about?” :-) Which is fair enough. I spent an entire afternoon struggling to say what I wanted to say, and I’m still not sure I said it very well. Which means it’s not clear in my own head. So consider this an invitation to help me think more clearly.