Missed this at the time, but back in December Charles Krebs listed what he sees as the 10 most important factors limiting the progress of ecology. Caroline Tucker of The EEB and Flow has just reacted. And so as an experiment in “blogosphere-style” blogging, I thought I’d quickly toss out my own reactions.
My thoughts, like his, are in the form of a numbered list, but my numbers don’t have any correspondence to his. I’m not commenting specifically on each of the 10 factors he lists.
1. I’m not entirely clear what Krebs would consider “progress”. I sense I’m not alone in this. Part of Caroline Tucker’s gentle pushback against Krebs is to suggest that his vision of what constitutes “progress” is too limited. She notes for instance that there are more ecologists than there used to be, more datasharing than there used to be, and more women in ecology. I admit that I’m unsure myself how to define “progress” myself. But while a precise definition is surely impossible, I do think it’s worth trying to be as explicit and precise as possible. By being explicit and precise, we prevent pointless arguments between people with different implicit definitions. Being explicit and precise also puts us in a position to draw on data (as in this recent post). So perhaps instead of starting with a (necessarily prescriptive) definition of what would constitute progress (or “fast enough” progress), we should start descriptively. Start by describing how ecology has changed over time, and how fast. Thereby providing a sound factual footing for a discussion of whether observed changes are progressive or not, or are sufficiently rapid. Relatedly, in an old comment thread Brian and I had an interesting back-and-forth on rates of progress in macroecology, and science more generally, and how one might measure them or judge whether they’re as fast as they “should” be (starts here).
2. The first two obstacles to progress Krebs lists are lack of jobs for academic and government ecologists, and lack of funding. At one level, it’s hard to argue with that. Any field will progress faster if you throw more people and money at it. But at another level, at Caroline Tucker notes there are lots more ecologists spending a lot more money than was the case even a few decades ago. So how many ecologists, and how much money for ecology, is “enough”? I have no idea how to answer that question. It kind of gets back to that exchange I had with Brian. How do you decide how fast a field of science ought to progress? And don’t say “as fast as possible”, because that just begs the question of what’s possible.
3. Some of Krebs’ concerns are to do with a purported lack of taxonomic and basic natural history data on many groups, arising ultimately because such work isn’t sufficiently valued. We’ve just talked about this and I don’t have much to add. I suspect he and I will have to agree to disagree on whether ecologists should focus more or less on model systems (which in ecology includes any system or location about which we already have extensive background knowledge).
4. Krebs’s complaint #6 is that that mathematical models too often are confused with reality, and that ecologists too often try to use math to “paper over” lack of data rather than properly linking models and data. I’m a little unsure what he’s getting at here. In my experience, it’s much more common for ecologists not to take mathematical theory seriously enough, rather than taking it so seriously as to mistake it for reality. And I’m not sure what he means by using math to paper over lack of data, or who he thinks is guilty of that. I mean, yes, there certainly are theoretical ecology papers that aren’t grounded in data–but that’s perfectly legit. There are lots of good reasons to do mathematical theory, and not all of them have to do with empirical data (see here and here, and Caswell 1988). Plus, there certainly are cases where we want to have practical theoretical guidance precisely because we lack data to guide us! Alternatively, if he’s complaining that too much theoretical work is unrealistic, well, R. A. Fisher would like to have a word with him. Anyway, for what it’s worth, I think ecologists have gotten better over time at linking models and data–that’s an area in which ecology has progressed (see here and here). And for what it’s worth, papers that do a good job of linking models and data clearly are highly valued, as that’s the sort of paper that mostly wins the ESA’s Mercer Award. Not that I don’t think there’s a lot of scope for further progress on linking models and data. But my own sense is that the reasons for failure to link models and data tend to be case-specific. Sometimes lack of data (or previous lack of data) is a big issue, as when people overgeneralize from the first few published empirical studies (and see this). But often lack of data isn’t the main problem. As illustrated by how many ecologists react when “data limitation” is relieved by the appearance of a massive new dataset that unfortunately conflicts with their own pet hypotheses. Or as illustrated by the fact that the intermediate disturbance hypothesis in its original form is still taken quite seriously by many ecologists despite a lengthy and very poor empirical track record (as well as a large body of theory undermining it).
5. It sounds like Krebs would like to see more emphasis on case-specific theory as opposed to highly-general theory. I note that there are prominent theoreticians who agree. Although again, there are times when general theory is exactly what you want, even for practical applications. Think for instance of the IUCN Red List criteria, many of which are based on general models of small, stochastically-fluctuating populations.
6. I second Krebs’ complaint that ecologists focus too much on trying to “test” imprecisely-defined concepts (and I love his term “pseudo-hypotheses” and might have to steal it!) That’s a big part of the problem with empirical work on the IDH, for instance–attempts to “test” imprecisely-defined verbal models almost inevitably just lead to confusion. And that’s also a big part of what went wrong with the phylogenetic community ecology bandwagon. I would only note that Krebs’ complaint here is somewhat in tension with his complaint about the proliferation of mathematical models. Math is precise, words aren’t. And I’d quibble with his chosen examples of imprecise concepts, in particular “stability”. Proliferation of alternative precise concepts that all fall under some broader heading (as with “stability”) is a slightly different issue than imprecision per se. I agree with Krebs that ecologists’ attempts to test stability theory have mostly floundered. But the problem isn’t that “stability” is imprecisely defined, it’s that too much empirical work has mixed up different precise definitions of “stability”, or not bothered to draw on any of the various precise definitions that are available. “Stability” isn’t a case of ecology lacking conceptual precision, it’s a case of ecologists failing to make use of already-existing conceptual precision.
7. Krebs complains that too many ecologists put the technological cart before the scientific horse. I agree that it’s unlikely that technology will just so happen to advance in such a way as to help us address whatever questions we most wanted or needed to address before the technological advance happened. And I’m sure there are technological bandwagons, just like other sorts of bandwagons. But on the other hand, it’s also unlikely that new technology will be completely useless. Krebs’ example of DNA sequencing is a good example of a technology that has both led to some real advances in ecology and to bandwagon-y, hammer-in-search-of-a-nail work. Which is inevitable, I think–sometimes the only way to figure out how to make good scientific use of new technology is to try it out. More subtly, our decisions as to what questions we most want or need to address always reflect the available technology, even if we try to make sure they don’t. So technological advances can–quite reasonably–prompt us to change our minds about what questions we want or need to ask. (At least sometimes; there certainly are technology-independent reasons for wanting or needing to ask certain questions.) Finally, just because some bit of science uses new technology doesn’t imply that it’s putting the technological cart before the scientific horse. I certainly hope Krebs isn’t falling into the same mistake as Lindenmayer & Likens, assuming that any work that uses new technology is probably bad science (see this old post of Brian’s for discussion of this mistake). Some ecologists have made the same mistake about every new technology that’s ever been invented. Back in the late 60s there were ecologists who were suspicious of computers. Yes, we should be careful not to put the technological cart before the scientific horse. But doing that is not as simple as just being generally suspicious of any and all uses of any and all new technologies. Much as one should not try to avoid statistical machismo by adopting a blanket, default suspicion of any new or complicated statistical approach. I think the only time one should adopt blanket, default suspicion of something is when that something has a consistent track record of failure.
8. Krebs’ complaint that ecologists these days are too specialized, and that this problem is exacerbated by their unfamiliarity with the older literature, is one that bears thinking about. Brian’s made a similar complaint about ecologists’ tendency to put old wine in new bottles, as have others. And we’ve talked in the past about ecological schools of thought, a topic related too (though not the same as) hyperspecialization. So I take this complaint seriously. But on the other hand, it’s often difficult to draw a line between worthwhile new work that builds on older work (e.g., refines it, tests it in a new way, applies it in a new context), and new work that just puts old wine in new bottles. Or demonstrates in a newfangled way what previously had been well-demonstrated in a now-old-fashioned way, or etc. Remember that even Darwin’s Origin of Species was criticized by some for just elaborating on (and failing to properly credit) the evolutionary ideas of its predecessors.
9. In general, it sounds like Krebs would agree with Brian’s complaint about ecologists’ lack of a “problem solving mentality”.
10. Krebs complains about failure of ecologists to all agree on what the big questions are and how to answer them. Brian’s complained about that too, noting that in fields like physics and astronomy there’s large-scale coordination of research effort. Others also have argued for more centrally-directed ecological research by coordinated teams. And one of the best ecology projects of the past decade is a centrally-coordinated, team effort. I do think we’ll see more centrally-coordinated work by large teams in future, a trend about which I confess to mixed personal feelings. I’m lousy at working in large, centrally-coordinated teams, or at coordinating such teams myself. I don’t enjoy it, and I don’t have the skills for it. And I also think and hope there will always be a place ecology for individual investigators pursuing their own ideas. There’s no way to force ecologists to all agree on what ecology to do; the entire field doesn’t depend on a few expensive shared instruments the way astronomy or particle physics does. And even if you could force ecologists to all agree on what to do, you wouldn’t want to because that would amount to putting all our eggs in too few baskets in terms of the questions we ask or how we go about answering them (at least, that’s my opinion). All of which is why I still don’t care what the biggest question in ecology is (well, I don’t care very much).
In conclusion, I just wanted to say thanks to Charles Krebs for writing down his thoughts and making them available. This is a good example of a topic that we ought to discuss publicly, but that isn’t best discussed by people writing and publishing peer-reviewed papers.