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.
Dynamic Ecology 
Sorry Jeremy, but what the hell are you talking about? [I absolutely could not resist!]
I’d have been disappointed in our commenters if no one had taken the bait. 🙂
Nice post! I’m also worried about the place of theory in contemporary ecology. In my opinion, the main problem is the poor philosophical formation of most ecologists. Many people are confusing theory and mathematical modeling: they are by no means synonyms. Mathematical modeling is a powerful tool, which can help build theories by making it easier to raise hypotheses with testable predictions. But it’s a tool, like many others, and there are alternatives. Theory in a deeper sense is strongly connected to philosophy of science and metaphysics, which many colleagues unfortunately regard as a waste of time. In journals, conferences, and classes I see ecologists arguing about how to measure, test or model this ou that phenomenon, but they seldom discuss the philosophical nature of the entities under investigation. Pick a simple example, such as biodiversity: there is much more literature on the operational proxies (which index to use) than on the theoretical meaning of the concept.
Thanks Marco, glad you liked the post.
In the post, I wasn’t actually thinking of theory in the philosophical sense you mean. Though it’s true that theory in that sense often isn’t seen as valuable in ecology.
Interesting post Jeremy! I hadn’t seen that quote from Levin but I really like it.
I’m not sure my objections stem from what you raise (the need for external criteria to judge theory).
For me I think it comes down to two things – one very general and one very specific.
1) On the general end – I profoundly believe that science is the balance between induction and deduction and it goes off the rails when one dominates. Think of the late classical Greek era with Ptolemy’s epicycles. Or much later phlogistons and ether (both worthy theories, indeed elegant, internally consistent etc, but with the one small problem they were both wrong which we know from empirical studies). This desire for balance and interplay is ultimately a philosophical opinion and so I cannot prove it, but I strongly believe it is true. If a theory isn’t attempting to describe reality than I don’t care about it.
2) On the specific, its not an objection to what could be mathematical theory in ecology but how it is practiced today – mathematical theoreticians are very often more concerned about challenging math and mathematical elaboration than informing ecology. I still remember a discussion with a famous theoretical evolutionist and he went on and on about how he solved a complex equation that even people in the math department couldn’t solve and I was too junior to say anything but I kept thinking “when are we going to talk about biology?”.This is different than the 1970s and people like MacArthur and May (or Levin) who actually care about the biology.And the why of why the 1970s were so different is a whole other post (have we already picked the low hanging fruit?)
Hi Brian,
it sounds like you’d say that Caswell’s “theoretical problems” are really mathematical problems, and so it’s up to mathematicians to decide if “pure theory” is valuable as mathematics?
Finding a minimum sufficient set of assumptions is definitely mathematical. Testing an alternative assumption – well if it is done to see which fits reality better than I wouldn’t call it pure theory, but yes some people do this just for intellectual interest – probing the model itself if you will. In which case these things sound very much like the stuff I did in my theoretical-only math major as an undergrad. So yes – more for mathematicians than ecologists in my book.
Jeremy, I was waiting for you to ask that question directly in your post. For example, we can’t just leave it up to ecologists to determine whether an abstract formulation of the question: “are more complex systems more stable” is productive. These sorts of
@michaelbode:
Your comment cut off partway through, repost and I’ll edit the thread to get rid of the incomplete comment.
1. If the epicycles hadn’t been invented by the Greek, you wouldn’t have had a case.
2 The epicycles were empirically accurate at that time. That a model with ellipses around the sun is a more parsimonious theory for the same phenomena is a subjective call (to which I subscribe btw).
3. When you wondered when the talking about ecology would start, you apparently weren’t grasped by the problem, and that may be partly so because you were not familiar with the equations and maths involved (like so many including me). For the specialists in the field, it has its own appeal. Lots of people don’t like jazz music or abstract art, but if one gets into it, one might learn to appreciate it. It broadens one’s horizon, and maybe someday it will help solve those problems that are more relevant. And if not, there will at least have been some intellectual growth. To summarize: I would probably have reacted in the same way as you did, but I just wanted to defend the pure theoretician who does not know how to make his research interesting to a broad audience, from his research being downplayed.
Maybe I’m now being boring by downplaying the divide, but isn’t this, at least partially, a question about the time scale at which theoretical models are evaluated. That is, are theoretical models “evaluated” over the longer term as a research program or as an individual study? If we go for the former, I can see agreement between Brian’s and Caswell’s quotes. Caswell is talking about purely theoretical developments, exploration and problem solving, which cannot be solved empirically (I hope I’m not misrepresenting this – I didn’t reread the paper just now). Brian (seems to be) saying that models “ultimately” have to smash with reality, to show that the theoretical findings seem to have some empirical bearing. However, this doesn’t exclude purely theoretical studies, but only that a theoretical research program is more powerful if it’s eventually evaluated against empirical data. Ok, Brain statement is stronger “…they’re not advancing science”, which I disagree with, but I still feel it is important to state clearly at what timescale/level we are talking about the usefulness of pure theory. To me, pure theory is useful if it can be made plausible (ie biologically meaningful/reasonable assumptions) even if it’s not tested directly against reality, but immensely more useful when “testing” is done.
Many of the negative statements against “pure theory” also seems to be against “bad theory”, as in models with unfounded assumptions and researchers that aren’t interested in the biological/ecological reality. This is fine and well (and a subjective judgement), but this is no different than “bad empirical studies” (empiry?); for some reason I don’t see the same problems raised about empirical findings with no ecological underpinnings or e.g. research that is shoe-horned into an ecological framework, even though the researcher is really only interested in taxonomy (which is fine, but often makes for uncompelling ecology). Or maybe these problems are raised, but then only labelled as “a bad study”. But for some reason cases of “bad pure theory” seems to spill over so that some consider all pure theory to be bad, while this is not the case for bad empirical studies.
I agree – time scale is important. And to be clear I’m OK with long time scales to smash against reality – it doesn’t have to be in the original paper. It just has to be a goal of the field at large and to happen ultimately.
And I agree that the distinction between bad theory and pure theory is also important, but I still don’t like “pure theory” if it means never testing it.
But if the evaluation period can be long (and variable?) then aren’t we basically back at determining if research is “progressive” or not, in Lakatos sense of the word? He discusses theoretical and empirical progressiveness (~predictive scope vs. confirmations of predictions), and that you over the longer term need to see both for the research program to be progressive. And this should be the case both for research with an empirical bias or a theoretical one.
@Tobias – well yes if there is a long and twisting road to test then it can be hard to tell right away if it is “pure theory” or theory with empirical applications. But that doesn’t eliminate the distinction. I think the intention of the author is often a good indicator up front.
@Tobias:
“But for some reason cases of “bad pure theory” seems to spill over so that some consider all pure theory to be bad, while this is not the case for bad empirical studies.”
Yup. There’s definitely an asymmetry here.
Interesting post, Jeremy! To me, what’s often missing in these debates about pure theory is the objective. Are we trying to understand nature? If so how our model or theory is useful to understanding nature had better be at the front of mind when we are designing it. Are we trying to solve an applied real-world problem? If so, we had better have the constraints of our solution at the front of mind (in my opinion, this is one of the areas where ‘pure theory’ type research goes awry most). Are we trying to advance a frontier of mathematics in an area that might be relevant to biology, but also might not? If so, then we should focus the presentation of our research on the math frontier and less on the (often tenuous) biological relevance.
On a perhaps slightly more controversial note, I disagree with the notion that which questions/approaches are interesting is wholly subjective and endogenous to science. I would argue that in most cases there is some objectivity in this. In ecology for example, all else equal, questions whose answers provide information about more systems are more interesting. All else equal, questions whose answers have more relevance to things the general public cares about are seen as more interesting (e.g. I would argue that scientific interest in the drivers of biodiversity was greatly increased by the emergence of evidence for a link between biodiversity and ecosystem benefits for humans. Another example would be the greater scientific interest in polar bear ecology than say, dung beetle ecology). All else equal, questions whose answers have implications outside of ecology are more interesting. etc. The unifying thread, in my view, in determinations of interest, is the societal awareness (both conscious and unconscious) that resources are generally limiting in everything we do, including in our quests to learn about the world, and this scarcity demands some level of prioritization and pragmatism. There are certainly some examples* where branches of science have gone off and defined more subjectively and internally what is interesting in a very detached way, but I would argue that these cases are the exception, not the rule.
Look forward to hearing what other people think!
*Large swaths of mechanism design theory in economics are one of the best examples I can think of of an endogenously determined interest with little practical relevance that spiraled out of control. Many of the seminal mechanism design papers seen have started from completely ridiculous assumptions (e.g. all people and the government can know all other people’s wealth and preferences), and shown that, under these assumptions, it is impossible to design a policy that meets a particular objective. i.e. if you are in a world that in no way resembles this one and you have a problem we care about in this world you can’t solve it. What?
Re: the “objectivity” of our judgements about what’s interesting or important, if we as scientists take our cues from society at large, then that’s just substituting society’s judgements for our own. I’m not saying it’s bad for us to do that–I’m just saying that there are still judgement calls being made.
Plus, society’s judgements as to what’s worth studying or spending money on often are pretty questionable. You don’t have to be an anti-democratic elitist to think so. Fundamental research in particular seems like a case where society is best off letting scientists decide what questions are interesting or important according to their own internal-to-science criteria.
I like that you added the caveat “all else equal” to each of your suggested guiding principles. But of course, the difficult thing is that all else is never equal, and those guiding principles (or any others one might name) can and often do conflict.
If you are framing your argument specifically on reality, then I think your comparison of “pure theory” and the mallard example is a false comparison. If “pure ecological models” are thought up in “pure ecology” land, then they are independent from an objectively observable reality. However, the mallard example is intimately linked to observable reality in that mallards are in fact widely distributed. It seems that in the mallard example the criticism is more about the sort of question one asks, but I agree with you that there are justifiable reasons to suggest mallards are interesting as well as uninteresting (depending on the particular questions you are asking about nature). Regardless of your views on mallards, if your interests follow observable truths and you explicitly test abstractions with reality I think you are informing our understanding of nature. If ideas, models, etc. remain untested, I agree with the others in that they serve little use.
Jeremy, I don’t think equating “theory” with “mathematical modeling without data” is helping the case of bringing theory and ecology closer together. In fact, it may be the very root of the problem that ecologists have with the word “theory”.
In most parts of science (and I see no reason why ecology should be an exception), the understanding is that theorists are the people that work on creating scientific theory. Scientific theory has a well-defined meaning, one can look it up on Wikipedia http://en.wikipedia.org/wiki/Scientific_theory : “A scientific theory is a well-substantiated explanation of some aspect of the natural world that is acquired through the scientific method and repeatedly tested and confirmed through observation and experimentation.”
And a quote from Albert Einstein: “The supreme goal of all theory is to make the irreducible basic elements as simple and as few as possible without having to surrender the adequate representation of a simple datum of experience.”
For me, theory = understanding of ecological mechanisms. And we get it like that: someone (I would call him a theoretical ecologist) creates a hypotheses about how the ecological world works. Empirical ecologists test that against data. Theory is revised if necessary. A theory without data is not “pure”, it’s “unproven”.
Mathematical modelling, specially the kind that deals with finding interesting mathematical cases and solutions for complex mathematical questions, is a fine thing as well. It has merit and sense as mathematical research. But it is not ecological theory, and we shouldn’t demand that acts as such.
Florian, please don’t try to settle a substantive debate with appeals to definitions. Fair enough if you want to say that “pure theory” as I’ve defined it is mathematics rather than ecology. But please don’t say or imply that consulting a definition on Wikipedia settles things!
I take your point about the definitions, but I do think it makes a difference if the thing we are discussing is called “pure theory” or “applied mathematics”.
If it’s called (pure) ecological theory, I expect that it should advance the theory of ecology, at least in the long run; and that necessarily includes the match with data because this is how we evaluate the merit of scientific theories.
Calling it “applied mathematics” changes my expectation. Mathematics doesn’t need empirical validation; if it does it’s not mathematics. If someone contributes to mathematics by finding the possible solutions to a particular predator-prey equation system, that’s fine with me. Maybe people working on ecological theory can later use these results for answering an ecological question, but maybe that never happens and its just a contribution to the mathematical literature.
I would argue that a lot of the reservations that you mention come from wrong expectations about the purpose / nature of the inquiry that is being done. Whose fault that is I don’t know, communication has always 2 ends. I might be inclined to put a bit more blame on the “pure theorists” that sell mathematical research in an ecological wrapping.
I think that a very important related issue is of understanding the motivation for a work. There is nothing wrong with navel gazing, and each community — experimental or theoretical — is just gazing at different kinds and sizes of navels. Sure, the navels of the experimentalists are often much larger since they can be linked to technologies or policies that affect lots of people and thus bring them — at least partially — into the discursive community.
But I think there is something wrong with advertising your work falsely, with building work that is of no interest to the community you are trying to sell it to but trying to disguise it as promising to them for whatever reason. This is what makes the mathematical biologist studying obscure biologically irrelevant properties of Lotka-Volterra uncouth. In their very title, they suggest that they are of relevance to the biological community but then produce work that is not actually relevant. At the same time, the work is often not mathematically pleasing enough to be relevant to the math community. This is something that I often see in interdisciplinary fields, you might advertise a paper to computer scientists as of great biological interest, and the same paper to the biologists as of great technical interest for computer scientists, when in reality neither field finds the problem interesting in itself. I am often very self-conscious when I walk that line myself.
Hi Jeremy, interesting topic. While this is clear that models linked to data are more and more popular, I am not sure that the distrust for theory is increasing – it might always have been there. However, given the large amount of untested theories that have proliferated in ecology, many mathematically-oriented ecologists suddenly find themselves in the position where it is perhaps more exciting to test the theories that are already there with new statistical tools and large scale data, rather than contributing to increasing an already high level of speculation. That would be my guess.
As for the reason of why criticism is so hard on mathematical theory, Fagerstroem noted we ecologists have often a misplaced trust in ecological data (both field and experiments) which are viewed as “hard facts” http://www.jstor.org/discover/10.2307/3566010?uid=3738744&uid=2&uid=4&sid=21104458402911 (think about e.g. nonrandom sampling of study sites).
Although there seems to be much debate currently about conclusions drawn from seemingly obvious data, e.g. are Yellowstone wolves really saving aspen?
“given the large amount of untested theories that have proliferated in ecology, many mathematically-oriented ecologists suddenly find themselves in the position where it is perhaps more exciting to test the theories that are already there with new statistical tools and large scale data, rather than contributing to increasing an already high level of speculation.”
It’s funny, that was very much my supervisor Peter Morin’s attitude about microcosms. Theories accumulate faster than we can test them, so we need experiments in “fast” model systems like microcosms just to keep up.
Thanks for the link to the Fagerstrom paper, don’t know that one, will have a look.
Question: where would any even *slightly* empirically-minded ecologist ever encounter pure theory (or applied mathematics, or mathematical biology, or whatever term you prefer)? I mean, theory and applied math journals are clearly labeled as such. 🙂 And to my eyes, hardly anything in any ecology journal anyone reads (even Am Nat) qualifies as “pure” theory. And I *highly* doubt that you could find any NSF DEB or IOS grants (or NSERC EEB section grants, or whatever) going to pure theory/applied math. And I bet the large majority of university departments that employ ecologists of any stripe don’t employ any applied mathematicians. So in practice, pure theory/applied math is well-demarcated from the rest of ecology. In which case–why complain about it? Or even take note of its existence? After all, ecologists don’t ordinarily take note of sociologists or chemists, much less complain about how they go about their business.
I guess one answer could be that some people (though probably not the folks commenting on this thread) have an overly-broad view of what “pure theory” is, and a correspondingly over-narrow view of how math can help us learn about nature. Think of E. O. Wilson claiming that “unrealistic” models are valueless: https://dynamicecology.wordpress.com/2013/04/07/e-o-wilson-vs-math/) Or think of that Simberloff piece to which Caswell was responding. So that they end up mistaking a lot of empirically-relevant theory for “pure” theory. But I don’t really know how many ecologists think that way.
Maybe we need a poll: list a bunch of theory/modeling papers of various sorts and ask people to vote on whether each is an example of “pure” theory. Or maybe grade their relevance to empirical ecology on a 1-10 scale or something.