A little while ago we invited readers to ask us any questions they wanted, and we promised to answer. We got so many questions that we’re splitting our answers across a few posts (probably one/week for the next three weeks or so). Here are our answers to the first batch. Thanks again to everyone who submitted questions!
On what questions in ecology do you hope the field will have made substantial progress by 2033? (from Margaret Kosmala)
Jeremy: Well, I’m on record as saying that I don’t care what the biggest question in ecology is. So maybe I should answer “It doesn’t matter!” That is, I’d just like to see us get better at doing ecology, better at addressing any and all questions that seem to be worth addressing. But that would be a little disingenuous, since I do in fact care more about some questions than others (everybody has their own interests). So by 2033 I hope we’ll have made substantial empirical progress in documenting the relative strengths of different classes of coexistence mechanisms, as defined by Peter Chesson. Stabilizing vs. equalizing. Dependent on spatial variation vs. independent of spatial variation. Dependent on temporal variation vs. independent of temporal variation. Etc. And how and why the relative strengths of those various classes of mechanisms differ (or don’t differ) between systems. More vs. less diverse systems (although it’s actually quite possible that “number of species coexisting” and “strength of coexistence mechanisms among those species” are independent of one another…). Aquatic vs. terrestrial systems. Etc. Basically, what I’m hoping for here is the community ecology analogue of the progress made in population ecology in documenting and understanding density dependence (and of course, intraspecific density dependence is closely related to interspecific coexistence…). Population ecologists now have a good handle on how strong density dependence typically is, what sort of systems exhibit what sort of density dependence (e.g., time-lagged or not), etc. In contrast, despite nominally being very focused on issues of coexistence, until recently community ecologists have hardly done the sorts of experiments one needs to do to address these very basic questions about how coexistence happens in nature. What we have done is mostly what I’d call “lower level” mechanistic experiments, asking about effects of removing predators or removing competitors or adding nutrients or etc. I’d like to see community ecology start at a higher level, equivalent to the population ecologists’ focus on density dependence. Community ecologists should focus first on documenting stabilization and equalization and whether or not they arise from spatial and temporal variability. We can worry about the underlying nitty-gritty, system-specific mechanistic details later. I have an old post talking more about this. One benefit of this approach is that, from this “higher level” perspective, community ecology looks way simpler and more unified, just as population ecology looks way simpler and more unified if you focus on high level processes like density dependence, or evolutionary biology looks way simpler and more unified if you focus on high level processes like selection, mutation, drift, and migration (again, see that old post). There is some great work along these lines out there already, for instance in plant community ecology from folks like Jon Levine, Peter Adler, Janneke HilleRisLambers, Amy Angert, and Stan Harpole. And I predict we’ll see more of it in future. I think it’s going to become a hot area, despite the fact that the required experiments are really difficult.
Brian: On the whole I am fearful for what progress means in ecology. Sorry to be a downer. For one of my written comp questions a decade or so ago, I did a review of recent plant competition literature. I took the top 100 papers in ISI with the phrase “plant competition”. I organized them into 14 themes. Then I looked at Clements 1929 book Plant Competition. He had 13 of the 14 themes in there. The language was much more anthropocentric (talk of wars between species), experimental rigor is much better today, and modelling and data are all much better today, but it terms of what questions we’re struggling with – no change. The only theme Clements missed was the role of spatial structure (i.e. spatial ecology). This story is a hard data point. One can make different interpretations. Maybe that is just how ecology is – it operates in a very complex high-dimensional domain. Or one could argue that something is wrong and we need to change how we do ecology and stick our necks out and make predictions (a running theme on this blog).
But leaving such depressing thoughts aside, I hope we make real progress on two topics: climate-organism interactions and (hopefully not unrelated) a trait-based view. When I was in grad school the climate-organism topic was seen as old hat – it went all the way back to the phytosociologists in Europe circa 1900 – and I was discouraged from pursuing it. Then magically climate change bubbled to awareness and it is a hot topic. But I don’t feel like we’re getting real traction yet – its more like we’ve gone back to documenting – hey! climate matters (see my previous paragraph). Physiologists have a deep understanding of the role of temperature on organisms but we have yet to scale this up successfully to communities or the globe. Many people are working on this, and it might just be tractable. The second is moving away from a species focused to a trait-focused approach. There is a lot of faddish useless stuff in trait literature right now (see previous paragraph, sigh!), but there is enough good stuff, I am convinced it will revolutionize the field.
What’s a good textbook for a beginner interested in doing predictive modeling, as opposed to, say, GLMs? And what are the most useful R packages for prediction? (from Tom Heatherly)
Brian: I would argue that GLM (and even OLS) are predictive tools, depending on how they’re used. But my favorite and top recommendation is Zuur et al’s book Analysis of Ecological Data. It is extremely well written. Adopts the basic approach of regression as a central idea (i.e. t-tests, ANOVA are really regression as are more modern things like robust regression and regression trees). The writers are very good at explanations. And the last half of the book is full of case-studies.
My favorite R packages in rough order of frequency I use them: rpart (for regression trees and don’t forget rpart.plot add-on and mvrpart package for multivariate dependent variables), quantreg (quantile regression), mgcv (GAM), nlme (mixed & hierarchial), robust (robust regression), fields (spatial interpolation), vegan (various), lmodel2 (Type II regression), segmented, strucchange (the latter two being two variants on piecewise-linear regression). And one that I haven’t used because I just didn’t see it being taken up in ecology but now has started to change is earth (mars or multivariate adaptive regression splines). I would add path analysis to the list if I felt like there was a great R package for it (let me know if you think there is on). If I were the stats czar of ecology, I would mandate much more use of regression trees, quantile regression, GAM and path analysis.
Jeremy: I just wanted to say that I don’t understand why Brian likes regression trees so much. 😉 Or path analysis, for that matter. 😉 And that I’m surprised that the guy who just accused ecologists of “statistical machismo” now wants to see us doing more multivariate regression trees and nonlinear mixed models. 😉 (Just teasing on all counts, Brian!) More seriously, if you want to do GAMs, you should also have a look at the vgam package, it’ll do some things that mgcv won’t.
Has neutral theory and phylogenetic community ecology been a distraction for the last 10+ years or have we gained true insight into community assembly and coexistence through this huge body of work? What is the future of these areas of investigation? (from AJ)
Brian: Can I say both? Specifically I think they were both great ideas that provoked good new developments. However, we went way too far. Specifically, just about the time we’d spent a couple of years and got 80% of the progress, dozens of grants got funded (due to the lag time in grant cycles) and we did a bunch of work that probably wasn’t fruitful. I can’t tell you how many papers I have been asked to review that “tested neutral theory” over the years. Probably 60 just for me personally. Which means there are probably at least 200 out there. Yet I wrote a review that came out in 2006 after the first 20 or so and I’m not sure we’ve learned a whole lot more since then by testing the theory (i.e. we knew then that neutral theory produces realistic SAD and SAR but not more detailed temporal or spatial patterns and that while the parameters appear to have mechanistic meanings they really only work as curve fitting parameters). That said I have to give neutral theory a major shout out for being a theory that took prediction seriously which is part of why it was so quickly tested. But I’m not sure more tests are telling us much. There has been some useful development of more neutral theory since then. And the main value is the response – the challenge to get serious about niches. I’m less up on community phylogeny – but I think the story is probably very similar, with the exception that this theory was never particularly great at making predictions and hence has not (will not?) be decisively tested.
Jeremy: On neutral theory, more or less what Brian said. I’d only add two things. First, it’s not just ecologists’ own data that should’ve told them much sooner when attempts to test neutral theory (especially with SADs) were reaching a point of rapidly diminishing returns. I think ecologists could’ve done a much better job of drawing on the long experience of evolutionary biology as to what tests of neutrality are or are not effective. Second, while testing predictions is great and all, the laser-like focus of testing predictions about the form of the SAD was disappointing. It’d have been much better if people had tried to systematically check all of the predictions of neutral theory, and test the assumption as well as the predictions. As any evolutionary biologist will tell you, there are all sorts of ways to test whether selection coefficients are zero (or more generally, estimate selection coefficients, estimate whether they’re frequency dependent, etc.) See, e.g., this old paper of mine.
On phylogenetic community ecology, I’d say it’s mostly been a distraction. Don’t misunderstand me, it’s totally fine for people to look for phylogenetic patterns in community data and then try to explain those patterns. I’m involved in a working group that’s doing something along those lines, and others have of course done that sort of work. But that’s not what a large and particularly trendy chunk of phylogenetic community ecology is about. I’m probably going to get slammed for saying this, but much of the attraction of phylogenetic community ecology is that it promises a shortcut. A quick and easy recipe to follow that purportedly lets you draw big conclusions about the mechanisms that generate community structure. I’m all for shortcuts when they exist (although they hardly ever do). Trouble is, the shortcuts phylogenetic community ecologists are taking aren’t shortcuts, they’re dead ends.
Now, in fairness, people working in the field insist that phylogenetic community ecology has gotten more sophisticated about the mechanistic inferences it’s trying to make and about how it makes them. I sincerely hope that’s true. We’ll see. In particular, as yet there’s been hardly any phylogenetic community ecology based on a modern (“Chessonian”) understanding of how coexistence works. And notably, the people I consider the leaders in testing modern coexistence theory just wrote a big review paper where they pretty much throw cold water on the idea the phylogenies, or any other easily-collected observational data, can on its own tell us much of anything about contemporary coexistence mechanisms. That’s not to say that you can’t combine phylogenetic information with other data (particularly experimental data) to learn about the mechanisms determining current community structure. But so far that’s not what most people are doing, presumably because that’s difficult and there’s no “recipe” to follow.
When I think of examples where phylogenetic information has really enriched our understanding of contemporary ecology (and vice-versa; knowing about contemporary ecology often helps us interpret evolutionary history), I think of bodies of work that that on Carribbean anoles, or on Darwin’s finches (other examples could be given). Those bodies of work are hugely rich and sophisticated, in terms of the ways in which phylogenies have been combined with other sources of data (including experimental data) to draw really interesting and reliable inferences about ecological and evolutionary mechanisms. I note that Mr. Phylogenetic Ecology (and Mr. Anole) Jon Losos himself recently took to the pages of Am Nat to more or less agree with me on this. Not that Jon’s infallible! But I find it reassuring that someone who, unlike me, actually does this stuff for a living sees many of the same issues I do.
What jobs outside of academia are eco-evo PhDs best qualified for? If you quit your academic scientist job, what would you do next? (from Susannah)
Brian: One obvious direction is working for the government. In the US, the USGS has many, many great scientists doing research (some of them embedded in universities). Other federal agencies are starting to pick up scientists again too (most biologists were moved to USGS under Al Gore). NOAA, various groups of the USDA and Dept of the Interior have strong groups of scientists and even NASA has some ecologists (remote sensing). The states also have many PhD level biologists. When I was in Canada it was a similar story: Environment Canada, Stats Canada and the provinces all hired a lot of scientists. These scientists range from still doing very basic research to very applied. A lot of NGOs (e.g. Nature Conservancy, Conservation International) increasingly are needing and hiring PhD level scientists. One of my lab-mates has risen high up in the science hierarchy at Conservation International and loves his job – he feels like he is making a real difference (and still doing research). It is possible, but hard, to make a go as an environmental consultant. Another choice would be in the communication/writing side. Everything ranging from an editor at Nature/Science to a free lance writer for journals like Nature/Science to New York Times and etc and of course there is education/outreach as well.
The writing/outreach jobs are a bit different (where getting practice doing popular writing/outreach is important), but my advice to prepare for the government and NGO jobs is to do great science, get it published, and pick up technical skills like statistics, GIS, programming and molecular techniques. Not too different for my advice to people pursuing academics. Near the very end of your PhD career you can start to see a fork between academia and government job tracks based on the journals you try to publish in, the meetings you go to, and who you hang out with, the importance of teaching experience, but that is just in the last year or two.
Jeremy: As I’ve written in the past, I did more or less quit ecology at one point, and my plan was to become a high school science teacher. Not so much because a PhD in ecology made me especially well-qualified for that job (in many ways, it either overqualified me or didn’t qualify me at all), but because that job had some of the same features I liked about my first-choice career. I know stuff, and I like conveying that knowledge. I like having significant freedom and responsibility to plan my own work, which teachers have in some respects (e.g., at the level of lesson plans). Schoolteachers have reasonable job security. Plus, my wife is a schoolteacher. So if you’re thinking of leaving academia, or worried that you might have to, my suggestion is to focus first on what you’d like to do rather than what you think you’re qualified by your PhD to do. In the comments on that old post, one ecology student said that her backup plan was to farm llamas. I’m sure you don’t need a PhD in ecology to do that, but so what? Don’t let your career choices be dictated by the Concorde Fallacy!
Beyond that, afraid I can’t say too much. People who’ve gone down one career path generally aren’t great sources of advice about other career paths. Academics like me often aren’t great sources of advice about non-academic career paths, just as non-academics often aren’t great sources of advice about academic career paths.
I think Brian’s advice is reasonable if you’re looking for a non-academic career path that could keep you involved in research. But if staying involved in research isn’t a key consideration for you, then I think you can cast your net much more widely than Brian suggests. For instance, I don’t think it’s necessarily hard to make it as an environmental consultant. Depends on the local market for environmental consultants and what sort of consultant you want to be, I think. Here in Alberta, there’s a big market for environmental consultants, at various levels (for people with bachelor’s, master’s, and doctoral degrees in ecology and allied fields). And I knew an ecologist who took some time off from his academic job to be a high frequency trader on the stock market. His quantitative skills actually were good background preparation for that.