Many posts on this blog are critical–we slay zombie ideas, we call out statistical machismo, we try to derail bandwagons, we praise contrarianism. As I’ve noted elsewhere, that’s emphatically not because I and the other bloggers here think all of ecology, and all of the ecologists who do it, are always wrong. Far from it! It’s just that those areas where we do have criticisms make for the most interesting posts. Posts that agree with the conventional wisdom, explain the familiar, and preach to the converted are mostly boring and don’t draw many readers. Further, even our most critical posts generally have a positive element–we suggest alternative approaches ecologists could take, alternative questions they could ask, etc.
But nevertheless, I decided that it’s time to take a break from the zombie slaying and contrarianism. Man cannot live by bread alone, as the saying goes (Blogger cannot live by zombie flesh alone? Ewww…) So this post is about ecological success stories, about praising the very best work that ecology has to offer.
What are your favorite ecological success stories? The very best work you know of? (You can define “successful” or “best” however you like) They can be single favorite papers, but I’m thinking more of bigger success stories than that. Lines of research, involving many people rather than just one exceptional investigator, and leading to successes bigger than could be encompassed in any single paper.
This would be a really long post if I tried to name all of mine, so I’ll just limit myself to a few of them (just the first few that came into my head).
One of them is the development and use of modern time series analysis and model fitting approaches to identify the mechanisms driving population cycles in many systems. See this old post for links to this literature. This body of work grew out of the decades old density-dependence vs. density-independence debates, and involved a lot of collaboration between field ecologists, theoreticians, and statisticians. It involved conceptual advances (e.g., understanding of stochastic nonlinear dynamical systems), empirical advances (e.g., data compilation), and methodological advances (e.g., in computationally-intensive approaches to model fitting). It’s hugely impressive stuff, a real and permanent advance not just in our knowledge of population ecology, but in how to do it. Read some of the links in that old post, and then go back and read something like Dennis Chitty’s memoir of his career in mid-20th century population ecology. You’ll really appreciate just how far population ecology has come. Chitty’s book, published in 1996, emphasizes his, and his field’s, collective failure to explain population cycles in small mammals. But the seeds for success had been planted and indeed were already sprouting. Now, less than 20 years later, population ecologist Peter Turchin has basically declared victory and moved on to applying the same methods to human history! (With how much success remains to be seen; see here and here)
Here’s another one: field experiments on interspecific competition. Ecologists below a certain age may not realize this, but there was a time in the late ’70s and early ’80s when “do species compete?” (or perhaps, “do they compete strongly enough for it to matter?”) was a really controversial question in community ecology. In large part, the controversy was conceptual or methodological, concerning the interpretation of observational evidence. I’ve referred to this controversy as the “null model wars”. And the response to that controversy is, I think, one of community ecology’s finest hours. People went out to the field and did experiments. Specifically, a whole lot of removal experiments, in which a species is removed from some randomly-chosen plots or sites, with others left as controls, and the effects of the removal tracked. As a result, we now have a clear-cut answer to the question “do species compete?” (“Yes, mostly”) We even have quantitative meta-analyses putting numbers and confidence intervals on the answer to this question (Gurevitch et al. 1992). Now, one can always hope for a better answer–more refined, more detailed, more precise, whatever. But frankly I don’t see that we really need one, and I assume most folks would agree, as evidenced by the fact that it’s been a long time since you could get a paper in a leading journal simply by conducting a removal experiment.
One could say something similar about top-down and bottom-up effects. Ecologists went out and did lots of similar sorts of predator removal/addition and resource enrichment experiments in lots of systems, and answered the basic empirical questions they set out to ask. For instance, when you remove predators, do you get a trophic cascade? Yes, mostly (Shurin et al. 2002). Same for effects of biodiversity on ecosystem function, at least if that very broad question is narrowed down to “effects of species richness within a trophic level on the total biomass, abundance, or resource use of that trophic level” (Cardinale et al. 2006). Say what you like about the limitations of many field experiments–they’re small-scale, or short-term, or whatever. The point here is, when we ecologists collectively decide that we really want an answer some empirical question that can be answered with relatively straightforward field experiments, we’re quite good at getting an answer. We should be proud of that!
I’d name some successes to do with management, conservation, and restoration as well if I knew them, and the research underpinning them, better. For instance, there certainly are species that have been saved from likely extinction, or at least quite widespread extirpation, via management interventions based on ecological research (American alligator, for instance). Or think of the acid rain story. Is it too early to label marine reserves a success story for marine conservation and fisheries management?
The point of this post isn’t to suggest some overall conclusion about how “successful” or “unsuccessful” ecology as a whole is. I have no idea how to quantify that in any meaningful way, and I don’t see much point in trying. All we can do is keep doing the best science we can, and keep raising the bar so that our best gets better over time. That means recognizing our failures–but it also means celebrating our successes. So tell us: what are your favorite success stories in ecological research?
Here’s a couple to start the ball rolling:
1) Neutral theory. By which I mean the theory itself was a brave and exciting and important theory. And within less than a decade the field had tested, digested, and assessed the theory and figured out the proper role (namely an extremely powerful mathematical framework, a great null hypothesis, an endpoint on a spectrum of niche-to-neutral dynamics, but not in any strong way an accurate description of how most systems work).
2) Spatial and temporal coexistence mechanisms (e.g. storage effect). Again great theory, great experiments, a clear sense of where we stand (an important mechanism found often)
3) Metabolic scaling sensu West, Brown and Enquist. The basic pattern was known for decades, and the claim of fractal branching networks as the cause remains not decisively proven in my opinion, and there are exceptions to the rule that have emerged (e.g. plant seedlings?), but the basic focusing on the importance and generality of this rule and the subsequent program of pushing this idea as an explanatory framework to its limits (and it did eventually reach its limits which is a victory for knowledge too) again all happened in pretty much a decade.
4) Not specific theories but the 1990s was a deacade where we went from hardly ever thinking about space or scale to almost everybody knowing they were really important (not that there is not still a lot of sloppy thinking in these areas but that is contrary to the point of today’s post)
I have mixed feelings about neutral theory. I think it should have been much clearer much sooner that it could not be tested by looking at species abundance distributions. And as for neutral theory as a “null” model, I’m actually planning a post in which I’m going to argue that that’s not the case, or at least not always. In many contexts (not all, but many), the “null” is a model with drift but no selection, but the “alternative” is a model with selection but no drift. So the models aren’t even nested, and neither is actually a “null” for the other. I don’t think this is a minor quibble at all, I think it highlights a very serious gap in the thinking of ecologists. Many ecologists really do treat “drift” and “selection” as alternatives, which as I’ve noted in old posts is just nonsense (https://dynamicecology.wordpress.com/2012/01/23/zombie-ideas-in-ecology-neutral-stochastic/). I think it’s too early to judge the ways in which neutral theory has really permanently advanced the field vs. merely being a trendy fad that didn’t teach us much vs. just being a source of new confusions. Could end up being some of all three.
Absolutely, Peter Chesson’s work on coexistence theory is a major theoretical advance (although not without antecedants, many of which aren’t as well known as they should be). The ongoing empirical testing is just beginning, as the recent review from Hille Ris Lambers, Levine, & co in AREES makes clear. But yes, the empirical testing that’s been done so far is some of the best fundamental work in community ecology over the last decade. And it seems like there’s momentum developing and we’ll see an accelerating rate of empirical tests coming out in the future.
Yes, I’d probably agree with metabolic scaling theory. The original WBE model is a tremendous creative achievement, impresses me as much as any paper I’ve ever read. Even though I gather it’s still not 100% clear if it’s empirically correct, or even exactly what one needs to assume in order to derive it mathematically. The various extensions of the original WBE model are a bit of a mixed bag. Some seem like very substantial advances in their own right, but in some cases, it seems like they’re basically just showing that different allometries are interrelated: A scales with B, and B scales with C, so C must scale with A, etc. And yes, I agree that that research program has reached its limits–do you think that’s widely recognized, though?
Not sure that “general recognition that space matters” is quite specific enough for me to count it as a big permanent advance, but yeah, I see what you’re getting at with that one.
I’d like to keep a Papers (the pdf organizer/reader) folder with “must read” ecology papers (a “classic” folder would also be good” so I’ve downloaded the linked papers from Jeremy. I have lots of the neutral theory and metabolic scaling papers but Brian, if you could recommend one Must Read in each of the areas that you mentioned that would be nice for me and probably other readers.
“All we can do is keep doing the best science we can, and keep raising the bar so that our best gets better over time.”
Quote of the day right there, for sure. I much appreciate what you and the others are doing here Jeremy.
Well this is a rather wildly vague and general answer, but I would have to put near the top of the list those patterns and processes elucidated more fully, or exactly, by remote sensing technologies. This includes especially, vegetation phenology topics, particularly leaf-out and leaf-off dates around the globe, two events which have very large impacts on things such as productivity, micro- and meso-climate, the global carbon cycle, hydrology, and many traditionally studied ecological (e.g. population and community level) processes at many different scales. And by technology, I don’t just mean the satellites and their sensors themselves, but also the increased power of various spatial pattern analysis techniques on raster data, techniques to correct for potential biases such as atmospheric and geometric distortions, and other technical issues.
I think one of the things that ecology (understandably I think, to some degree) suffers from is the lack of global data sets. Remote sensing is the very big step forward in that regard, although of course, there are only some types of information that can be collected from satellites. In my view, the tying together of information arising from different sources and characterized by different spatio-temporal scales, resolutions and error characteristics, is at the heart of science, and I think remote sensing is going to go a very long way indeed in helping us tie together those disparate pieces of information. For example, a lot of folks are working on how to related imagery to quantitative, on the ground, vegetation measures, such as forest structure and biomass.
Thanks Jim, that’s a very good answer, one that probably wouldn’t have occurred to me.
For me it’s the whole edifice of mechanistic movement models, and various extensions, like Brownian Bridges. I think it’s a good demonstration on how theorists, statisticians and empirical and experimental ecologists can work together to build and test models. A small sample of some of the cool outcomes:
Explicit predictions about like how quickly a population front can move, what data we need to collect to test that, and what sorts of model will not be easily predictable, given movement mechanisms and population dynamics
Simple rules-based models of how complex groups like swarms and schools form
Methods to test what mechanisms are contributing to the shape of an individual home range
A great theoretical (and testable) framework to determine how an organism will move across the landscape and interact with other species/themselves/the landscape, from IBMs to movement kernels to diffusion, advection-diffusion and reaction-diffusion models.
Going back to an old post, I think movement ecology has also given us some great shortcuts to test our theories. Want to know how fast a species is moving? How large an animal’s home range is? Whether the population is exhibiting longer-range than expected given how far it moves on average? Net squared displacement over time is a great first stab that gives you a great many answers, and strongly constrains the set of possible hypotheses that can explain a species’ dispersal pattern.
The application of nestedness theory (sensu islands) to species interactions invigorated a lot of ecologists interested in mutualistic relationships, particularly plant-pollinator and -seed dispersal. The earliest work was by Jordi Bascompte and colleagues in the early 2000s. Likewise the use of network theory for understanding how these interactions are structured has given deeper insights into assemblage-level patterns and processes.
Hmm, not sure I can agree with you on that one, Jeff. In part because I’m not sure what you mean by nestedness “theory”–you mean just taking data on “who pollinates whom” and calculating a nestedness metric from those data?
And I think the theoretical models that people have used so far to explain those data have some serious shortcomings. I definitely wouldn’t say that we “know” that assemblage-level patterns have interesting underlying causes. It seems to me that a lot of major patterns in observed network structure can be explained as rather uninteresting sampling artifacts or epiphehomena. For instance, a lot of the features of existing bipartite network data can be explained just by undersampling of rare species and interactions. And a lot of the remaining features are rather too easy to explain. Existing metrics of network structure are pretty coarse, in that it’s pretty easy for a model to predict them well even if it predicts “who pollinates whom” quite poorly. I have an old Oikos paper that makes a similar point in the context of food webs.
No, by nestedness theory I was referring to the body of work that had preceded its application to interaction webs – see the following for a historical introduction: http://www.uvm.edu/~ngotelli/manuscriptpdfs/UlrichConsumersGuide.pdf
It was some inspired lateral thinking that took this earlier work and showed how it could be applied to species interactions as much as islands or habitat fragments.
There are many exciting aspects to this (and to network theory more broadly) but I’ll list just a few:
1. Mutualistic interactions (of all types, including marine animal-animal relationships) tend to structured rather differently to predator-prey or host parasite relationships and are far more often nested in structure. If nestedness is really just a sampling artifact, why don’t these other assemblages also show nestedness? Why would they not also suffer from “undersampling of rare species and interactions”?
2. Abundance of a species within a community is a fundamental ecological property. So even if nestedness was simply an “epiphenomenon” of relative abundance, that’s still interesitng ecology.
3. However relative abundance is only part of the story of why some species are generalists, others are speciialists, and the majority of mutualistic interactions are generalist-generalist and specialist-generalist, with few (actually zero in most assemblages) specialist-specialist relationships. Other important parts to this relate to trait matching – see work by Martina Stang for instance.
Thanks for the further comments Jeff. I suppose I’d see this body of work more as work in progress that hasn’t yet attained the status of a substantial advance, except perhaps at a purely descriptive level. We now have lots more data on who pollinates whom than we used to, and many more descriptive summary metrics of network structure than we used to.
Re: your #1, That networks of plants and pollinators have somewhat different structure than, say, food web networks doesn’t seem all that surprising to me. I mean, one’s a bipartite network and one’s not. And I didn’t say that nestedness is purely a sampling artifact, merely that sampling artifacts are important. If memory serves, Diego Vazquez has some recent work on the contribution of undersampling to our current picture of what typical plant-pollinator networks look like.
Re: your #2, I guess we’ll just have to agree to disagree. To the extent that nestedness and other plant-pollinator network properties can be explained as a byproduct of relative abundance, I don’t think that’s very interesting. Sure, abundance is “fundamental”. But if some feature of the world is just some rather obvious consequence of variation in abundance, I personally tend to find that feature of the world rather boring. Perhaps that just says something about me, I don’t know. I’m sure what each of us finds “obvious” or “boring” is a quite personal matter to at least some extent.
Re: your #3, this gets to why I don’t think this work yet counts as a substantial advance. My reading of this literature is that for most networks we can explain some of who pollinates whom by appeal to (what seem to me to be) rather uninteresting mechanisms–and that we can’t really explain the remaining variation at all. That is, I have the impression that attempts to do “trait matching” mostly fail, at least when applied at the whole network level (as opposed to the level of “this extraordinarily long-spurred flower is pollinated by a moth with an extraordinarily long tongue to match the spur”) Much the same is true in the food web literature–we can get some way towards explaining who eats whom in some systems with fairly obvious explanatory variables (e.g., predators eat prey that are smaller, but not too much smaller, than themselves), but it’s very difficult to do much better. In food webs, Andy Beckerman, Owen Petchey, and Phil Warren have made what I think is the most interesting and ambitious attempt, parameterizing optimal foraging models from data from feeding trials, and using them to predict who eats whom. For some food webs they do impressively well–but for others the approach fails rather badly. As I say, I think this sort of work is well worth pursuing further, but I don’t think it’s yet had many big, clear-cut successes. In the plant-pollinator literature, what do you see at the most successful attempts to predict who pollinates whom via trait matching? Stang’s work (which I’ll need to look up)? Possibly, I’m unaware of very successful work in this area.
Perhaps I didn’t explain it properly but the important advance to me, and why I consider it a success story, is that it applies not just to plant-pollinator mutualisms but also to ALL other mutualistic interaction networks that have been studied so far, both marine and terrestrial, plant-animal and animal-animal. See for example or work on anemonefish-sea anemone interactions –
Click to access Ollerton2007-FindingNEMO-ProcRoySocB.pdf
[Though in this case the scale at which the nestedness is found is across the whole distribution of the interaction rather than at an assemblage level, for reasons that are not clear].
That seems to me to be a very powerful (and predictive) ecological finding: mutualistic assemblage structure is different to other types of structure. In relation to your comment that :
“networks of plants and pollinators have somewhat different structure than, say, food web networks doesn’t seem all that surprising to me. I mean, one’s a bipartite network and one’s not”
Yes, but parasite-host webs are also bipartite and they are generally not nested.
On your other point that:
“if some feature of the world is just some rather obvious consequence of variation in abundance, I personally tend to find that feature of the world rather boring. Perhaps that just says something about me, I don’t know. I’m sure what each of us finds “obvious” or “boring” is a quite personal matter to at least some extent.”
I agree with your last point, but a huge amount of ecological theory has as its starting point changes in population size over time!
As for #3, yes. you should look at Martina’s work; it ticks the boxes your describe.
Would add more but have to dash; off to see The Hobbit movie tonight!
All the best,
Given your interest in economic theory, I thought this might intrigue you:
Thanks Jeff. Traveling now, only looked at the abstract, looks interesting.
HI all, my vote for greatest success story in ecology is Schindler’s whole lake experiment in the 1960’s that identified phosphorus as the limiting nutrient and the cause of algal blooms in that lake followed by Dillon and Rigler’s paper (and subsequently others) that showed the effect of phosphorus was ubiquitous. It was, I think, the first of the whole lake experiments, it played a major role in regulatory policy and led to basic understanding of how lakes work (as illustrated by how well P levels predict chl levels). best, Jeff H.
That’s a great pick, Jeff.
The work of Dan Janzen in general. Specifically, his restoration ecology in Guanacaste Costa Rica is the best example I know of showing how ecology as a science and natural history can guide conservation policy, ecological restoration, and advance ecological science.
Hi Jeremy, we come down on different sides on the importance both of modern time series analysis and field competition experiments. I’ll start by saying that I think these were tremendous methodological steps forward but relatively minor steps forward in our understanding of the natural world. I’m on much thinner ice discussing the population dynamics work because I’m relatively unfamiliar with it but I’ll make a couple of comments – even where we have an enormous incentive to make good predictions (spread of disease), Keeling et al (2008) show that their predictive accuracy is 5 to 15% (the index of accuracy is not straightforward and I will take some time to understand it better but for the moment accept it as reasonable, on faith). And they use models that, at least to a neophyte like myself, don’t bear much resemblance to the models have been developed to predict lynx, hare, larch budworm abundance etc. There are all kinds of places where we would like to be able to predict population abundance (fisheries, agricultural pest management, disease control) and I would be interested to know how widespread the use of these kind of modern time series analyses approaches are in these fields and how successful they have been at predicting abundances. Are we doing a significantly better job of predicting fish stock abundances today because of the development of these models than we were doing 20, 30, and 40 years ago using variations on the Ricker or Beverton-Holt models? Maybe we are – I just haven’t seen any claims that we are getting much better at predicting abundances. This discussion has sent me back to Peter Turchin’s ‘Complex Population Dynamics’ and with any luck I’ll be able to write more cogently about this over the next several months.
On the competition story I feel a little more competent to comment. And I think that the fact that you and I might feel that providing the answer to the question ‘Do species compete?’ is a major success story causes me a moment’s pause. People have been weeding their gardens, and foresters thinning their plantations, and cattle and sheep farmers killing each other for centuries because they know that species compete. And this is not meant to be an attack on ecologists – if I’m throwing stones it’s from inside the glass house. This perspective arises from a deep dissatisfaction with the work I’ve done for the last 15 years and a sense that I need to aim higher. And I mean one simple thing when I say aim higher – if I make the claim that my work has contributed to our understanding of the natural world, have I provided evidence that the statement is true? “ I don’t believe that “Yes, species compete.” is a large contribution to our understanding of the natural world. I’m not totally convinced that it’s even a small contribution.
The wide range of questions that people might care about and don’t know the answers to include “What is the relationship between competition strength/intensity and extinction probability?”; “How does that relationship change with the extent you examine?”; “How does that relationship change depending on the life history characteristics of the focal species?”; “How does that relationship change with the abiotic conditions?”; “What is the relationship between the abundance of two competing species in natural systems?”; “How is that relationship affected by multiple competing species?” And so on. Complex questions. Perhaps, unanswerable questions in the face of natural complexity. But, it seems to me that when somebody asks us a question like “If purple loosestrife invades my wetland how will the abundance of bluejoint reedgrass change?” our answer is usually “It depends.” – until we can make a a prediction in response to that question it’s difficult to stake claims to how much our understanding of competition has increased due to field experiments.
So, while I admire the work that you mention, Jeremy, done by very smart people working on very difficult problems, I am not convinced they are tremendous success stories. Perhaps they are, in relative terms, but, if so I think it implies that (i) it is difficult to demonstrate progress in ecology, and/or (ii) we rarely demand demonstrations of progress in ecology.
Thanks for the opportunity, as always. Jeff H
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