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.
I think he’s basically right on the money. Of course you can always find some point or other to argue about in a list of ten, but as a holistic assessment, yeah, I think he’s got it right.
But we still don’t have a definition, and I don’t think I agree with the idea of gleaning one by looking at how ecology has changed over time, because change itself is not necessarily progress of course. The decline of taxonomic and basic species or organism level investigations (some would refer to these as “natural history”) is change, but it’s certainly not progress.
To me progress in ecology is not defined by the frequently assumed standards of academia. It’s defined by how well we can predict things, and more specifically by how useful is the information provided to policy makers to help in solving practical problems. If theory and mathematical modeling helps get you there, great!; go for it, know what you’re doing, and do it well. If it’s instead “stamp collecting” to get some better, specific knowledge about your system components…then so be it, get that information. I’m not much impressed with those who think theory/generalization constitutes some kind of Holy Grail in and of itself. It doesn’t, and people with that view have held sway in ecology for too long now. It’s in fact very narrow minded in my view.
Yes, absolutely, changes over time aren’t necessarily progressive. But if you think things have changed in a certain fashion, when in fact they haven’t, there are going to be tears before bedtime if you try to have a discussion about whether those non-existent changes are progressive or not. For instance, think of Lindenmayer & Likens’ claim that mathematics and meta-analysis are crowding out other sorts of papers in the ecological literature. That’s just false, and so there’s no point arguing whether it’s a good thing or a bad thing. It’s not a thing at all! That’s the only point I wanted to make.
Yes, but the assessment of whether certain things have changed in a certain way/direction, or not, itself has a subjective element. For example, I’m by no means certain that the claim by L&L you cite there is “just false”. I’m not sure that it’s true either; I really don’t know, and it would take a very major effort to try and make an evaluation on the question.
Relatedly, I take definite issue with your statement: “Math is precise, words aren’t”, both as a stand-alone statement, and as an argument against Krebs’ point. As a stand-alone, I think that is a humongous over-simplification of various concepts involved in language and meaning. As a response to Krebs, I don’t read Krebs’ point #6 as arguing against mathematical analysis per se. I hear him saying that it’s all too easy to throw together yet another mathematical model, perhaps of questionable usefulness, than it is to evaluate existing models by collecting the data needed to test them. Essentially, I think he’s arguing against sophistry, not math itself.
RE: “I hear him saying that it’s all too easy to throw together yet another mathematical model, perhaps of questionable usefulness, than it is to evaluate existing models by collecting the data needed to test them.”
This is a good point, but I would argue that it is suboptimal to put the onus on model/theory people to test their theories. For one, they may not be very good at it. Both modeling/theory and fieldwork/ experiments are skills that require lots of time to build proficiency. There are some that seem to do an amazing job being quite proficient in both, (or get grad students/post docs to fill their weaknesses), but for the rest of us, some division of labor is required. Another probably more important reason, is that the particular person who developed a theory is the least biassed person to test it. Ideally, the people testing a theory should have as little to gain from a confirmation/ rejection of the theory as possible. Instead they should be judged by how well suited the experiment/ fieldwork tested the applicability of the theory.
For me this makes the case for better collaboration among the theorists and empiricists. Although I don’t know how good or bad this collaboration is in ecology relative to other fields.
Hi Jeremy – nice response. As I mentioned in my post, I also agree with a lot of what Krebs (and you) are saying. I think what I was responding to is more that there are tons of these “what is wrong with ecology” type lists and posts out there, but so rarely do we consider “what is right with ecology?”. I think it would be great for the ‘blogosphere’ to spend some time identifying positive trends in ecology too 🙂
” I think it would be great for the ‘blogosphere’ to spend some time identifying positive trends in ecology too”
Thanks for the excuse to link back to this:
Hi Jeremy, I’m disappointed if we can’t even agree on what would be defined as progress in ecology. It seems to me that there is really only one measure of progress that makes sense in just about any scientific discipline – “How much more do we understand today than we did yesterday?” Now, measuring that may be tricky but that’s what we should be trying to measure.. Best, Jeff.
I’m surprised that you of all people would stump for “understanding” rather than “predictive precision and accuracy” as the criterion for progress, Jeff! 🙂
Don’t get me wrong, I’m all for “increased understanding” as a, or maybe even the, criterion for progress. But what if, say, our understanding grew over time primarily through greater understanding of model systems, rather than growing at an even rate “across the board”? I suspect that some ecologists (including me) might be ok with that, while others might not be. Or to pick another example, should progress be measured solely or primarily in terms of our ability to provide managers and policy makers with the information they’ve already decided they want or need? So that “fundamental” progress is either irrelevant, or is relevant only insofar as it improves our ability to provide future managers and policy makers with the information they need?
At the broadest-brush level, I actually don’t think it would be too hard to get wide agreement on what constitutes progress. But when you start digging into details, that’s when I think you’ll find that not everybody agrees. At least in terms of how to prioritize different things that everyone agrees are worthwhile at some level.
Hey Jeremy, I’m at the point now where I use understanding and predictive ability interchangeably because I don’t think there is any other way to demonstrate understanding than with prediction. And if you can’t demonstrate understanding then, in my opinion, it’s the same as not having it. So, not surprisingly, I think you measure progress by increases in predictive ability (i.e. understanding).
That said, I think you’re right that some people would say that increases in predictive ability in areas that don’t provide commercial applications or make significant contributions to policy shouldn’t be weighted as heavily. That would be a useful discussion but not one that I would see as derailing ‘progress’ discussions.
And progress in understanding model systems (and I know you’ve heard this criticism before and don’t agree with it but your arguments against it haven’t convinced me) is only progress to the extent that they help us understand the systems they are intended to model. The fact that we call them model systems implies that they are being used with the intention of understanding ‘real’ systems. If they help us understand those real systems then they are absolutely demonstrating progress. If they aren’t used to make predictions in ‘real’ systems but are only used to make predictions in the model systems then the progress being made is much more speculative.
“progress in understanding model systems…is only progress to the extent that they help us understand the systems they are intended to model.”
Sorry, but as you know I’d deny your assumption that model systems need to “model” some *specific* natural system. They can also aid our understanding in other ways, for instance by expanding the range of variation beyond what nature provides us and so allowing us to see what would happen under conditions that would never occur, and could not be created, in any natural system.
Thanks for all your comments. Just a few points. I completely agree we have made progress in ecology. Gad, I write textbooks and I see it all the time. The question I wanted to ask is can we do better and if so how. One answer is that we are already going as fast as possible and there is little we can do to go faster. But I think this is not right and so I ask if you are a pure ecologist do you not have a big project you would love to do but have no money, or helpers? Or if you are a wildlife manager or conservation biologist, do you not have questions you would like to answer, perhaps by new technology or more money, or better hypotheses? At any rate when I read the conservation literature about species X going to hell in a hand-basket I see many questions for which we need answers for management that we do not have for one reason or another. I agree progress is a slippery word but we know it when we see it.
Regarding models, I of course like simple statistical models, R.A. Fisher, ANOVA, now AIC and good population projection models. These really are in my mind technology for answering questions about empirical relationships and we have progressed well in this area (but please do not bury us in p values). What I do not favour are models that have no connections to empirical reality and make no predictions or are full of unmeasurable parameters. So Lev Ginzburg is my hero for sweeping at least some of this away. But I do not want to stop modellers as I think science advances in quite unpredictable ways and no one can pretend to be God. I think the most successful linkages are of modellers and empirical ecologists continually interacting, and we need to foster more of this.
At any rate thanks for your comments, as I think this is like a global tea time discussion that keeps us thinking about what we do.
Re: funding and people, I wonder about the trade-offs between different sorts of funding systems here. Yes, like everyone I can imagine great research projects I’d do if I had a lot more money and people. But I don’t want to do those projects enough to want to move to an NSF-style system of big, hard-to-get project-based grants. I want to be able to sustain a long-term research program and spend my time pursuing it rather than chasing money. I’m risk-averse, I don’t play the lottery in real life and I wouldn’t want to spend time and effort playing the “NSF grant lottery” either. Of course, arguably the relevant issue isn’t my attitude to risk, it’s the funding agency’s attitude. Scientific advances are indeed quite unpredictable–but surely there are some advances that can only be made by spending large amounts of money. In light of that, what’s the optimal funding allocation system? Hard question.
Interesting that you would raise Lev Ginzburg’s work in passing. I’m among those who think ratio-dependent predation is unhelpful both from a phenomenological, I-just-want-a-flexible-equation-I-can-fit-to-empirical-data perspective, and from a conceptual or mechanistic perspective. But obviously, opinions vary widely on this. Ratio-dependent predation is one of those polarizing ideas that some people love and others hate…
Pingback: FLUMP – Featuring RA Fisher’s 124th Birthday, smog sequencing, and a traits manifesto | BioDiverse Perspectives
I have been told off by a Forester on a well-known public site in Australia when I dared to mention the word “stability” in a postt as apparently the ecologists had gotten rid of the idea in the 1980s so I was behind the times!
In terms of stability I like Kauffman’s work on order and complexity and recognise that stability is found through increased order leading to complexity, and find it important that he notes that a system can readily be stable even though non-equilibrium and dynamic (according to the maths or something), so my bugbear is not with concepts of stability although clearly there is a marketing problem with the wider community! It is with equilibrium which in chemistry appears to be related to such a high degree of order that it is best exemplified by a regular crystal. Thus this would mean equilibrium in a forest might mean a tree every x square metres in a regular pattern! I think Kauffman’s point that stability can occur in non-equilibrium situations is vital for ecology to take on board, and that the word equilibrium not stability should be BANNED. If said it should only be in the context of a stable system TENDS TOWARDS equilibrium more than does a more completely non-equilibrium system exhibiting randomness characteristics. Clearly a forest can be stable over several hundred years, clearly it is not as highly ordered as a crystal with entropy zero, so just as clearly non-equilibrium, and because there is change over geological time, also dynamic. In the case of the Australian/Antarctic Nothofagus forests, they were present for close on 50+ million years, albeit with various extant as the continents dried. There is stability over long periods but biota is subject to the same thermodynamics rule of entropy as the physical states are, so unlike the crystal biological states are probably never going to be at equilibrium, even though organisms show high order such as in the function of organs, and forests show efficient nutrient, energy and moisture recycling, as well as community composition, such that there is resiliance to disturbance, hence a degree of stability.
Sorry that’s bugbear one out of the way!
Bugbear two is why, in times of crisis such as the planet seems to be driven to by us, there is not a Biotron. That is, there is an international collaborative and highly expensive search for the machinations of particles, as there should be, but where it comes to ideas like Gaia there is zilch. Ok this may be an airy fairy idea, but whether or not the planet functions as one system, that is, conjoined physical and biological processes, is surely fundamental to determining how it responds to climate change, water deficits, soil degradation, pollution, ocean acidity and depletion and the list goes on (sorry if I missed the crisis you are working on!). So it really doesn’t matter if the models are based on a united system, completely separate physical and biological systems as many geologists,soil scientists and others would have us believe and base their studies on in practice, or two intersecting systems, with an intersection having unknown properties. In fact why have a basis for studying or modelling anything, why not just go along randomly and add bits and pieces here and there to the info! It is no wonder scientists within and between disciplines are not agreeing, there isn’t a fundamental basis to do so. At what point are these crises going to get so bad that it will be realised it is absolutely urgent to find out the fundamental basis for modelling Earth’s processes, that is, as one system (Gaia of Lovelock), as two separate systems, or as two intersecting systems? At what point will it be realised that it would be a good idea to have a synchotron in biology in which international collaboration from both physical and biological scientists can work out how the system actually works on a macro scale, before it actually collapses?
Have just read 2012 synthesis of milestones in ecology on this site. Very interesting, makes me realise how much more I have to know though, it has all become a little mind-boggling from when I did my degree years ago. Part of it I think is that there are great teams and individuals out there just doing there own thing, which sometimes pulls everyone along. But I think it may be worthwhile having a page here on what COULD be progress in the next few years. One of the posts on the 2012 blog discussed GIS and satellite. Yes, but there are some minuses. Where I live in a regional area there are no local experts to speak of so what happens is sometimes they send a team up from the capital city a few hundred kms away, but much of the taxonomic work as mentioned may not have been done, and noone including me is employed to do much else. They just use satellites, modelling and a team of experts in the city and the rest goes to wrack and ruin. It is tremendously disheartening at the state level, and even worse at the federal level since the new government has just axed everything good as soon as they got in. First to go was a carbon scheme that included a Biodiversity Fund. So progress in satellites and computer technology is just used as an excuse to get rid of everything and everybody else, so although there may be progress in ecological knowledge, there is no progress in policy implementation. In fact there is almost no policy- the idea of sustainable growth has become a complete joke in Australia. And on the world stage climate negotiations involve world powers who use the meeting to discuss other things such as nuclear proliferation.
However said that ecological progress has not resulted in progress in the governmental level in many places, in fact I am not sure that they know what progress is at all in my country, technologies such as GIS are very promising, not for progress achieved but for what they will be able to do. For example, 3D modelling has immense potential to examine landscape interactions between say nutrients, catchment, and biota. My guess is that protein studies are going to rock the foundations of biology and genetics and therefore of ecology, probably in the next decade which will be greatly enhanced by 3D modelling. I was very interested to read the 2012 discussions about network models in ecology, but I am not sure they are going to be complex ENUF. I think that for this very sophisticated 3D modellng and accompanying mathematics will be required. I wouldn’t discount chaos theory (fractals) so readily either. Whatever ecology has achieved in the last 50 years one thing it has shown is that the probabilistic nature of the atom and thus the universe is reflected in the probabilistic nature of the ecology, since of course one is derived from the other, and thus stochastic wins out over deterministic, but this makes analyses much more difficult. The discussion about modelling taking over real field work troubles me but then I was troubled by satellite replacing it too (and to some extent still am) but find MODIS analyses of biomass etc. really wonderful, and hope that modelling will, although perhaps consumptive of journal space etc., also force us to move forwards. This will involve more sophisticated mathematics and 3-D modelling in the next few years though.
I think there has been immense progress so far, but as I said it is a somewhat confusing information overload unless you have been keeping up with it year in year out. The profusion of information is only going to get worse, and progress may involve some effort to synthesise it all, if not at least to find out where the contradictions are.
Progress IS understanding, understanding the natural world, but overall progress as mentioned in my post above entails an understanding of how the biotic and the abiotic relate. Without that we have a biota without a planet or a planet without any biota (as in the early Archaeon),and that is where I think there has been failure to progress, because that is by necessity interdisciplinary, and takes a really concerted effort. However that form of progress along with a huge improvement in governmental approaches will be essential lest the crises that face the planet are not to overcome us. For the ecological sphere though, I think there needs to be some progress in synthesis of information, to establish directions for research.
Pingback: Poll: which purported problems with ecological research are actually problems? | Dynamic Ecology
Pingback: Death by a thousand cuts – Geekcologist