Commenting on my recent post on the need for more “short selling” (i.e. criticism) of ideas in ecology, Jeff Houlahan asks a good question:
When was the last time we had an in print debate that matched the heat and light of Diamond versus Connor & Simberloff? Or Andrewartha and Birch versus Nicholson? I’m sure there are more recent examples but they don’t come to my mind.
Let’s crowdsource the answer. Name some vociferous-but-productive (“heat and light”) debates in ecology, either historical or current. And just for comparative purposes, name some that were unproductive–all heat, no light. In the past I’ve speculated on why heated debates in ecology get started (it’s often not for any obvious scientific reason). But the productivity of the subsequent debate is a separate question.
A few opening bids:
Productive: the debate over whether effects of plant diversity on primary productivity are purely “sampling effects”. A narrow debate, to be sure. But a productive one. An important issue was raised, and then resolved to the satisfaction of pretty much everyone (there are always a few holdouts) through a combination of new data and new analytical techniques.
Unproductive: Tilman vs. Grime on plant competition along productivity gradients. I freely admit I never followed this debate very closely, so maybe lots of people will disagree with me on this and tell me what a rich, interesting, and productive debate it was (is? is it still going?) All I can say is that I didn’t follow it closely because when I looked into it briefly many years ago, my foxy sense* warned me off. The sort of mathematical framework that people like Dave Tilman (and me, and basically everyone I hang out with) use to think about competition is just so different from the sort of primarily-verbal models people like Phil Grime use. There has to be some sort of agreement on basic terms, concepts, and goals in order for a debate to be productive, and I’m not sure the necessary baseline agreement was there in this case (again, please enlighten me in the comments if I’m way off base here…) One offshoot of this debate (well, I think it’s an offshoot; maybe it’s a whole separate thing?) has been what is in my view a pointless side debate over alternative indices of the “strength” or “importance” of competition. In general, I think debates over alternative ways of measuring something that lacks a precise agreed definition run a higher-than-normal risk of being unproductive. See, e.g., the debate over alternative ways of measuring alpha and beta diversity. Such debates are arguments about definitions, disguised as (or mixed up with) arguments about substantive issues, and that’s a recipe for disaster.
Not sure: has the debate that Joan Roughgarden started about sexual conflict theory in evolution been at all productive? Early on, I had the impression that the answer was no, that Joan’s criticisms of established thinking were idiosyncratic and implausible at best. But I’m an ignorant outsider, and I haven’t followed subsequent developments in the field at all. Have any productive new lines of work emerged from Joan’s criticisms?
If we get enough responses, we can attempt a comparative analysis of the features associated with productive vs. unproductive debates in ecology. For instance, just from the examples suggested so far, the breadth of the topic under debate does not seem to predict the productivity of the debate. There are examples of both productive and unproductive debates over narrow issues, and over broad issues. Which is a little surprising. I might’ve thought that narrower, more “technical” debates would be more productive because it’d be more likely for all sides to agree on definitions, goals, background assumptions, etc.
*Foxy sense is like Spiderman’s “spidey sense“, only instead of warning me of physical danger, it warns me of unproductive arguments that would be a waste of time to follow. 😉
Dynamic Ecology 
The arguments about the Mid-Domain Effect in the mid-aughts were about as nonproductive as you can get, I think.
Yeah, I’d agree with that. Debates that never needed to happen in the first place (say, because they were prompted by the need to refute a bad “null” model based entirely on a Narcissus effect…) are unproductive almost by definition.
Just went back and read your take on MDE. (https://dynamicecology.wordpress.com/2012/08/30/why-do-our-null-models-nullify-some-effects-and-not-others/)
I’m choosing to not respond well, fitting the point of the post, that’d be an unproductive debate.
Ok, I’m smiling, but I’m not quite sure why; you kind of lost me. 🙂 Did you actually find the MDE debate unproductive for quite different reasons than I did?
If you change your mind about wanting to respond to my point of view on MDE, you’ll get another chance soon. 😉 There’s an old-wine-in-new-bottles post in the queue on how “null” and “neutral” models are overrated, and overused as a research approach in ecology. I mention MDE in passing…
More evolution than ecology, but the group-selection vs. inclusive fitness debate has been raging for decades, it seems. You’d think the massive negative response to Nowak, Tatnita, and Wilson would have settled it, but it never dies, for instance, there is a forum article promoting group selection to appear in Behavioral and Brain Sciences (the call for commentaries ended on May 1st).
Benton v. Alroy. Is there a limit to global species richness? Have we ever been anywhere near it? What is the appropriate way to scale diversity patterns in the fossil record, and fit models to them? I’ve had to wade through this in preparing a book chapter and frankly I’ve lost any of the interest that I started out with.
In productive debates I’d count the niche arguments up to the 1950s. Though the arguments then stagnated and entered several dark decades of neglect (temporarily unproductive), they laid the groundwork for later synthesis by Tilman, Holt and others (see e.g. Chase & Leibold 2003 Ecological Niches).
Benton vs. Alroy isn’t one I know, thanks.
Debates over neutral theory were productive for a while. Forced a recognition that stochasticity was important and forced niche theory to sharpen its arguments and become more predictive (albeit niche theory is still fairly weak as a mathematical theory). However, too many people who wrote grants to test neutral theory were still trying to weigh in after the ship had sailed and the productive part was over.
Was punctuated equilibrium a productive debate? My instinct says no, but it’s not something I followed too closely.
Was the top-down vs. bottom-up effects debate productive? It certainly had unproductive elements. But I’d say it was productive overall, as it prompted a lot of people to do the experiments that eventually answered the most basic questions the debate posed. Similarly, the pushback from folks like Gary Polis against conclusions drawn from early compilations of food web structure data led to collection of much better food web data and better conclusions. And the already-mentioned “null model wars” (Diamond vs. Connor & Simberloff) eventually led people to conduct lots of field experiments on competition, which settled the basic questions at issue.
I’m going to go ahead and call that a generality: when a debate is about an empirical question that can be settled with straightforward experiments, it’s productive. The debate prompts people to go out and do the experiments, and once we have enough of them to do a meta-analysis, the debate is over.
My vote for a productive debate would be the ongoing one about whether Levy walks are optimal foraging strategies, and the related question of whether animals use Levy Walks in the real world. The original theoretical work introduced an interesting new type of movement model with substantially different dynamics compared to the correlated random walks everyone was focusing on previously. Further, they suggested when and where we’d expect to see different foraging strategies. The pushback on theoretical and statistical grounds raised the level of empirical work and introduced mixtures of random walks as an alternative, and testable, model. While I’m generally of the opinion that true Levy-Walk behaviour is rare, I think the whole debate has substantially improved how we think about and measure foraging behaviours. I think we’re still waiting for the definitive meta-analysis and theoretical synthesis to finish that debate off though.
Interesting. That’s a debate I’ve followed a little bit. Wasn’t sure if it was productive or not; glad to hear it’s actually going somewhere and people are learning something.
So the debate follows a true Levy-walk? 🙂
“So the debate follows a true Levy-walk?”
Erik Verbruggen for the thread win…he shoots…he scores! The crowd is going wild! 🙂
you’re welcome…. your assist was invaluable, though 🙂
Just to add a few precisions on productivity of Levy walk / flight models there – there are strong grounds to disagree. The only productivity I can see to this Levy flight “debate” is to put foraging theory in the spotlight again at a time when it was sinking into oblivion.
There’s been mixtures of random walks routinely used in movement analyses for at least 10 years, yet (1) these have not been motivated by LW models (papers by e.g. I Jonsen, JM Morales et al.) and (2) many empirical papers now try to prove LV models are “optimal” because physicists said so, however that makes absolutely no biological sense. Open a classic textbook on foraging theory, e.g. Stephens and Krebs 1986, and one soon reads that we cannot test whether foraging strategies are optimal. We only test if given an optimality criterion (like in economics, some utility is maximized), some strategies are better than others. It then all depends on the “phenotype set”, as Maynard Smith would have put it.
Theoretical LW models have been compared to Brownian motion, which is known to be a highly inefficient searching strategy since the 80s. The reviews of foraging theory from that period mention it in passing; should your prey be Poisson distributed, you’re better off moving in a straight line. So much for novelty. In practice, “empirical LV modelling” means fitting power-laws to distances moved, while curiously discarding autocorrelations between steps and turns that are the nuts and bolts of movement analysis. In the original LW model there are also no such autocorrelations, but for some reason many LW fans prefer to focus on marginal distributions than autocorrelation functions (that’s easier I reckon).
To me the LW debate is the hallmark of the unproductive debate, because the debate is not over a biological question but whether some model fits best. What do we learn when we know distances moved fit a power-law at the individual level? How do we know we should look at this quantity? We still don’t how the animal allocated its time / choose directions and why it did so…which is generally why we track them.
Another example of model-fitting where researchers fell in love with the model seems ratio-dependent functional responses. Again the debate is not on the biology, but on which model is “best” – but best for what?
Well said Fred. As I said, I personally don’t know anything about the movement literature, so you and the other commenters can battle it out on whether the idea of Levy walks has been productive. But on ratio dependent functional responses, I’m very much with you, at least at the moment. As I say, Lev and Roger’s new book is in my reading queue, and I plan to write a review for this blog once I get around to reading it.
Just to add a date to when mixture models entered the scene—Brian Stott had a paper in the Journal of Animal Ecology from 1967 analyzing dispersal as a mixture of normals…. (http://www.jstor.org/stable/10.2307/2922)
In the field of mycorrhizae there is a debate on whether the fungi can sometimes be labelled parasitic or not (see recent commentaries by Smith & Smith, and Johnson and Graham, in Plant and Soil). My take on it is that the discussion is very much about semantics, instead of the real ecology of these organisms, so not very productive. Without offense, I would summarize the argument the following way: do mycorrhizal fungi on purpose sometimes reduce plant fitness (then they are parasitic), or do they do it by accident (but don’t mean to; then they are not)?
Antropomorphism intended with a pinch of sarcasm.
How about the 2/3 vs 3/4 power scaling of metabolic rate with body size? The way I understand it there has been no solid conclusion either way and both camps are just clinging to their pet theories, with no middle ground. To me it seems to be rather unproductive, but I think that the overall question has led to some interesting modeling and research in metabolic theory.
Hmm, interesting suggestion. On the strictly empirical question of whether the true scaling exponent is “really” 2/3 or 3/4 (and the related debate over whether there’s “really” just one universal slope, or “really” different slopes in different taxonomic groups that just so happen to average out to 2/3 or 3/4), I’d probably agree with you that it’s not been productive. On the theoretical side, it was my impression early on that the West-Brown-Enquist model both had a lot going for it, and was going to spawn a lot of really new and useful work (both new modeling, and new data collection) that would retain its value even if the WBE model turned out not to pan out. And I think it has, though I admit I stopped following the latest developments over the past few years.
All of which is probably a long-winded way of saying “I agree with you.” 😉
I would have to disagree and say that there is a very decisive conclusion that 3/4 is better than 2/3. There is debate about whether to force a rational fraction or just leave numbers like 0.78 and 0.72 as is or treat them all as a signal of 3/4. And there is debate on some exceptions (bacteria), seedlings, field metabolic rates, that might be higher than 3/4.And I think it is fair to say that the mechanism in WBE behind 3/4 has not been decisively proven, although I would have to call it the front runner. But 2/3 is not seriously in the discussion due to repeated empirical tests.
Now the related 3/2 vs 4/3 self-thinning law in plants is still debated (although the idea that the 4/3 comes from the 3/4 is rather compelling).
maximum parsimony v. total similarity in phylogenetics was a RAGING debate that spun its wheels for about 10-15 years in the pages of syst zool (and the halls of Stony Brook, Michigan, etc.) until junhyong kim, rohlf, & sokal actually decided to do Monte Carlo methods to test the efficacy of the different methods with known (made-up) phylogenies under different models of evolution. These were just computer-intensive versions of how sokal taught numerical taxonomy going back to the 70s using the Caminalcules (which are still are great tool for teaching phylogenetics). The basic idea was then picked up by Hulsenbeck and Hillis and others.
Can’t believe I forgot pheneticists vs. cladists! Good on you for mentioning it. A long time ago philosopher David Hull used that debate as a case study of how science advances, arguing that science advances in a process broadly analogous to evolution by natural selection. The book’s called Science as a Process, if memory serves. Very interesting book, though at the time I read it, I wondered if Hull hadn’t done himself a bit of a disservice by choosing as his case study an atypical scientific debate. Though this thread suggests that perhaps there’s no such thing as a “typical” scientific debate…
Don’t most debates in ecology end up with the answer, “it depends on the system at hand?” Top down or bottom up? It depends. Single large or several small? It depends. 2/3 or 3/4? It depends. Competition regulates community structure? It depends. And then the argument leads to experiments that than can sort out the specific circumstances that shape the ‘depends.’ Not the undergarments.
Oh man, the SLOSS debate! Forgot about that one too. David Ehrenfeld, the first EiC of Conservation Biology, told me as a grad student that he eventually decided to stop publishing papers on SLOSS because nobody had anything new to say. So there’s one person who found that debate unproductive, or at least found that it quickly became unproductive.
Re: is the resolution always “it depends”? Well, sometimes, but not always. It depends. 😉 In part, it depends in part on the level of quantitative detail at which you frame the debate. If the question under debate is a qualitative one, like “do top down effects occur?”, or “do bottom-up effects occur?”, the answer is “yes they do, pretty much wherever and whenever we look for them”. If the question is a more quantitative or mechanistic one, like “what drives observed variation in the strength of top-down effects?”, then the answer is some combination of “it depends” and “we don’t know”.
Actually there is a recent paper that I like quite a lot on SLOSS http://lifeserv.bgu.ac.il/wb/yziv/media/Yaacobi_et_al-2007b-Fragmentation-Proc_Royal_Soc_B.pdf showing in part why there never was an answer.
I agree the answer is always it depends. The big issue is whether we just quit the debate by saying it depends and stop. Or if we start enumerating the depends and saying decisively under these circumstances it goes this way. Under those circumstances it goes that way. We should do the latter, but I think we mostly do the former. I can’t think of too many well-enumerated cases of how the outcome varies depending on some factors.
Sometimes you don’t want a debate to be productive. Regardless whether you consider Gleason or Tansley the killer of organismic ecosystem conceptions, I guess it chimes with your predilection for killing zombies.
On second thought, besides debates that appreciated and debates that are not, there is probably also the absence of debate that is salutary and the absence that is not.
“besides debates that appreciated and debates that are not, there is probably also the absence of debate that is salutary and the absence that is not.”
Good point. In part that’s what I tried to get at in that old post asking why some ecological and evolutionary questions are controversial. Which questions we *do* have debates about isn’t necessarily the same thing as which questions we *should* debate.
I certainly don’t think we should just have debates in ecology for the sake of having debates. But I do think there are some debates we should be having, but aren’t. As my own efforts to start a debate about the zombie intermediate disturbance hypothesis illustrate.
How about ratio vs prey dependent functional responses? I haven’t followed the debate close enough to say how productive it has been. For the systems I have worked in, ratio-dependent functional responses seemed like a bit of a stretch within the range of naturally occurring predator densities. Although a model with a ratio-dependent functional response would probably fit a daphnia-algae system better, this would also be true if you added just about any stabilizing mechanism.
I think that debate was productive in the sense of clarifying areas of agreement vs. disagreement. For instance, all concerned eventually agreed that predator dependence in functional responses is probably a big deal which hasn’t gotten enough attention from empiricists doing feeding trials to measure functional response shapes. And all concerned agreed to disagree on other issues.
Lev Ginzburg and Roger Arditi have a new book out (“How Species Interact”) which they say substantially advances the debate, and makes a strong case for ratio dependence. I haven’t seen the book, so I can’t really comment. All I can say is that the blurb on Amazon.com sounds more like a rehash rather than like a substantial advance. In particular, it sounds like Lev and Roger are still focused on ratio dependence specifically rather than on predator dependence more broadly. And Lev and Roger apparently are still trotting out what seem to me to be *extremely* weak indirect arguments in favor of ratio dependence based on the fact that it predicts that both predator and prey abundances will increase with enrichment–a datum that has all sorts of explanations having nothing whatsoever to do with functional response shapes. That’s always been a particular sticking point for me personally–Lev and Roger seem quite keen to take data that arise from all sorts of ecology having nothing to do with functional response shape, and then ask if that data is better captured by a predator-prey model with a ratio dependent or prey dependent functional response. To which the correct answer seems to me to be “Why should I care?” Or perhaps, “Why do you think that that question is a good one to ask if the goal is to explain the empirical data you claim to want to explain?” Don’t get me wrong, I plan to read the book and consider it carefully, and I’m prepared to change my mind. But as with anything I read, it’s up to the authors to convince me.
As for whether ratio-dependent models could fit a Daphnia-algae system, I think that depends very much on what you mean by “fit”. You didn’t say what you meant, so I totally don’t want to put words into your mouth. So let me lay out what I see as two alternative possibilities, or perhaps two ends of a continuum, as to what one might mean. If you just mean something like “reproduce qualitative changes in time-averaged algal and Daphnia biomass along enrichment gradients”, sure. In previous publications, that’s roughly what advocates of ratio dependence have meant by “a ratio-dependent model can fit Daphnia-algae dynamics.” Frankly, I think that’s an awfully low bar, indeed so low that I don’t really see the point of jumping it. But speaking as someone fortunate enough to count Ed McCauley as a colleague, that’s not what I think one should mean by “fit Daphnia-algae dynamics”. What I want from a model that “fits” Daphnia-algae dynamics is more like “quantitatively reproduce the various quite distinct types of stage-structured cycles and predator-prey cycles that Daphnia-algal dynamics exhibit, and the stochastic and deterministic factors that cause the dynamics to flip from one sort of cycle to the other”. The simple ratio-dependent models with which I’m familiar don’t even attempt that. Instead, Ed McCauley and colleagues continue to make hugely impressive progress quantitatively explaining Daphnia-algal dynamics with mechanistic models that build up from knowledge of the life history of individual Daphnia. (Those models use *prey-dependent* functional responses, by the way, so the limiting case if you remove all the stage structure and other life history details is a prey-dependent model, not a ratio-dependent one) So I really cannot see the point of applying Lev and Roger’s simple little ratio-dependent models to Daphnia-algae dynamics. Simple models totally have their place–but it is not “explain Daphnia-algae dynamics”! Trying to use simple ratio-dependent models to interpret even a few limited features of Daphnia-algae dynamics would be a positive hindrance rather than a help in learning where those dynamics come from. Nor do I see how one could possibly claim any feature of Daphnia-alge dynamics as evidence for a simple ratio-dependent model.
p.s. Let me emphasize that I’m *totally* not criticizing you, Ben! Sincere apologies if it came off that way. Indeed, I’m guessing that you actually more or less agree with what I wrote. But you unintentionally touched a nerve by referring in passing to the possibility of using a ratio-dependent model to fit Daphnia-algae dynamics. That’s a topic I know something about, and I consider one of the biggest success stories in population ecology. The whole idea of fitting a simple ratio-dependent model to Daphnia-algae dynamics and thinking that you’d learned something significant by doing so (or that you’d discovered significant evidence for ratio dependent functional responses by doing so) really bothers me as a scientist.
No worries didn’t take it as criticism, and I couldn’t agree more with your points. I too really like the approach of the McCauley group. Shameless self-promotion, but if you are interested in that line of work you might want to take a look at recent paper (http://www.jstor.org/stable/10.1086/669904) specifically Figure 7, and the discussion. Basically we conclude that juveniles having a higher resource-dependent mortality than adults in our model and the one used by the McCauley group is the key factor that promotes small amplitude cycles.
*facepalm* JEEEEBUUS I’m embarrassed Ben–I saw that paper, really liked it–and TOTALLY forgot you wrote it! God, I’m an idiot, spewing all that stuff in my last comment when I could’ve and should’ve just said “Hey everybody, Ben himself, who is too modest to toot his own horn, just did a really cool Am Nat paper that you should all go read, showing how to *really* learn about Daphnia-algae dynamics.”
Climate-driven vs. anthropogenic extinction of Pleistocene megafauna. This one is so utterly dependent on getting the temporal baseline right for a given region (i.e. when did humans get there). It has thus gone back & forth between papers describing the dominance of one or the other factor, depending on the latest. most precise dating of events.
Great topic: when we have a debate about debates we’ll advance meta-science! cool.
I’m tempted to add to the list of half-productive debates the one about whether the notion of “exotic” or “alien” species is relevant to invasion biology. I don’t know the whole history or aspects of it, but two different episodes come to mind:
2007: Charles Warren criticize the role of the concept, Dave Richardson and other VIP answer.
(http://phg.sagepub.com/content/31/4/427.refs; http://phg.sagepub.com/content/32/2/295.refs?patientinform-links=yes&legid=spphg;32/2/295)
2011: Mark Davis and 18 other VIP brought back the debate in a Nature comment. Many more answered.
Productive? well, it hasn’t really yield new tracks for testing hypotheses, as the question really depends on how we define “relevant for invasion biology” and its dependences (“harmful”, “invasive”, “wanted”…). But the debate still is relevant in a world where communities are more and more reshuffled, and having conservation oriented researchers take a step back and ask social scientists for help is good, I think.
I should also mention a similar debate about whether trait studies are useful (eg, can we predict a species’ invasiveness from its traits?) . Again, it is usually a question of definitions, and the debating part of the topic is not very useful. But the studies it brings forward are.
Oh and some more fuel to the fire of the “alien species” debate, pushed to the extreme (calling the end of the field!!!!!)
http://onlinelibrary.wiley.com/doi/10.1111/j.1600-0706.2013.00445.x/abstract;jsessionid=1A8C65279B047367FDD4320AEF82E9AE.d03t04
“Is blogging a useful tool for advancing ecology?”
My vote’s for unproductive, but I’m still willing to be convinced otherwise 😉
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