Here’s a notion: When we discover a big new thing, this often requires an abandonment — or at least serious doubt — of a commonly accepted notion.
I’m about a third of the way through Rob Dunn’s brand-spanking-new book about the human heart. I just finished the parts about the science of the heart before the 1900s. People always have had ideas about the function of the heart, and for most of human history, these ideas have been really mistaken. One influential person might establish an untruth as fact, and that fundamental error (albeit reasonable in its social context) might be inherited for over a thousand years. For example, that’s about how long it took for people to realize that the heart did not pump air, I just learned.
In his previous two books, Dunn also shared the stories of many other scientists who made discovering by doubting commonly accepted truths. He points out to us, time and again, that much of the world is not known. That includes the world which we are currently looking at straight in the face. Carl Woese doubted that all single-celled organisms were bacteria. Lynn Margulis didn’t buy the party line on membrane-bound organelles. Lyell didn’t assume that the surface of the earth was static. And so on.
I think chatting with elementary students about your research might be the best way to ferret out those assumptions. They’ll be the ones who will really wonder about the fundamental assumptions because they (hopefully) haven’t been trained to buy into them yet. If someone asks a question, and we can only muster a vague it is known, then maybe… it’s not?
So, to make huge discoveries, you just gotta set your mind free, you know man? You just gotta toss your assumptions and incorrect dogma and then you’ll be able to know better than everybody else around you. If only.
It’s such a fine line between stupid and clever. Doubt correct dogma, you’re an ignoramus. Doubt incorrect dogma and show that you’re right, you’re a visionary.
Some of the foundational ideas in ecology must be wrong, just as they must be in any other discipline. I’ve got to wonder which foundational ideas in ecology are flat-out wrong, or pointless, in a way that’s constraining or misdirecting progress.
I spent about 20 minutes writing and deleting a bunch of ideas. I’m not ready to share overly wacky ideas that I can’t buy into. But, on the lighter side, I’ve ditched the principle of competitive exclusion, I’m tired of the pervasive temperate bias, and while it’s abundantly clear that current theoretical frameworks aren’t build to understand the evolution of sterile workers in social insects, I don’t have a better one for sale. (I do think that people are overlooking the role of behavioral and developmental canalization that happens after functional sterility evolved, and it’s a little silly to have to explain the adaptive nature of reproductive decisions by females that had no choice but to be born without the structural capacity to have productive sexual intercourse and probably were also endowed with a bunch of other genetic baggage that undermines what would be in the interest of their genes that they’re not passing on, but that’s not in my sandbox.)
I suppose there’s something to be said in here about the Kuhn, Popper, paradigm shifts, and the Structure of Scientific Revolutions but, at the moment, that’s not how I’m rolling. But y’all are more than welcome to share, as always.
So basically, spent 20 minutes writing a list of zombie ideas? :-)
You say you’re ditching the competitive exclusion principle; I’ll be curious to hear exactly what you mean to ditch, and why you’re ditching it. The competitive exclusion principle is one of those things where imprecise words are a poor substitute for precise math. And it’s value isn’t as an empirical statement or prediction about nature. It’s a conceptual statement about what happens in a limiting case.
Clearly, the math of (at least some) competitive exclusion models is valid, and can represent what has been seen in the lab and in the field, at least sometimes. One species can exclude another.
But the way it’s taught in books — though not necessarily considered by practicing ecologists who think about community assembly — people act as if two species with identical niches can’t coexist with one another. While that might be the case in a temperate rocky intertidal zone, that can’t really describe what happens in a tropical rainforest. It’s not to be thought of as a guiding principle.
So, yes, it happens in a limiting case, as you say. I was making the point that the conditions limiting this case are so great that maybe we thinking about it gets in the way more than facilitates? (This is where I avoid saying anything less-than-optimistic about mesocosms because I want to be sure to finish manuscript revisions today rather than engage in an interesting discussion, which is probably one that you’re used to.)
For context, one of the things I deleted was about the notion of community “structure.”
Interesting. Your suggestion here Terry–that the limiting case of competitive exclusion only helps us think about what’s going on in depauperate systems, not in hyperdiverse systems–is one I’ve run into before. And I confess it puzzles me. I mean, yes, I get that a system with a whole bunch of species just seems really different from one with just one (though I would question whether species richness is the right metric of “different” here–a system with a whole bunch of species might differ from a system with only one species by only a single coexistence mechanism, e.g., a strong storage effect as suggested by Chesson & Warner for coral reef fish). But I just don’t see why that makes it any less useful to know what happens in the limiting case. Indeed, if you think that high-diversity systems demand an explanation precisely because they’re diverse (which I think is the common view), then aren’t you implicitly conceding that the limiting case of competitive exclusion is relevant? After all, isn’t it the contrast with that limiting case that makes high-diversity systems so surprising, so in need of explaining? And if you find that, say, the Janzen-Connell mechanism (or whatever) generates strong intraspecific density dependence in tropical trees, and you conclude that that explains the high diversity of tropical rain forests, what you’re saying is that, if you removed that mechanism, then intraspecific competition would be weaker than interspecific competition and so the competitive exclusion principle would operate. So even if you don’t consciously think of yourself as using the competitive exclusion principle, it’s implicit in your reasoning. I mean, how else are you supposed to explain why the world is the way it is, then by asking how the world would be if things were different–perhaps very different?
The other thing I’d say is that part of value of limiting cases is as check on our pre-theoretical intuitions. Insofar as you have incorrect intuitions about what would happen in some simple hypothetical limiting case (and many ecologists, including me, do), how could you have a snowball’s chance in hell of understanding what’s going on in a complicated realistic situation? My recent Friday link to Servedio et al. (http://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.1002017) makes this point. Now, I suppose you could just deny my claim here and argue that the artificiality of simple limiting cases makes them weirdly difficult to reason about compared to complicated but realistic situations. So that training ourselves to get better at thinking through deliberately-simplified scenarios is a waste of time at best. At which point I’d probably ask you when you’re planning to rewrite every single textbook in ecology and every other field of science, because deliberately-simplified limiting cases are part of the core conceptual content of every field of science as far as I know.
At this point, I think I’m just recapitulating my old post on limiting cases in ecology and moral philosophy, so I’ll just shamelessly link to it. :-)
https://dynamicecology.wordpress.com/2013/10/10/on-the-value-of-simple-limiting-cases-lotka-volterra-models-and-trolley-problems/
If what we see in limited cases is caused by mechanisms that do not operate under more common circumstances, then using reasoning derived from these limited cases can only make the matter more complex.
I think you’re making my case, to some extent, in that we are held captive to ideas, and our thinking is chained by key assumptions.
I’m of the opinion that attempts to explain high diversity are what gets us in this big mess in the first place. This is a manifestation of the temperate bias that I mentioned. The only reason that (some) ecologist have a compelling NEED to explain the biodiversity in the tropics is because it’s higher than they’re used to in the temperate zone. It’s rather arrogant for temperate biologists to waltz down to the tropics and seek to explain the diversity down there. If we don’t approach biodiversity to be solved, but a fact of evolutionary history and ecology, and them move on to explain mechanisms of low diversity in the temperate zone, we might come up with different theories. This principle of competitive exclusion is born of the temperate zone. All of the mechanisms and theories that emerge from this principle, or take it as an assumption at the root (such as Janzen-Connell), and diversity corollaries of trophic cascade models, might not be able to provide any answers to ‘diversity’ either.
Species richness of a region – the species pool – is simply predicted by speciation rates and extinction rates. Whether or not you have a given number of species occur in a certain location, assuming perfect sampling, is a matter of who manages to get pulled out of the species pool in a given sample. What’s the relationship between speciation, extinction, and species richness? Does having a lot of species inhibit the emergence of new similar ones? I don’t think there’s evidence for this, but I’d love to have that conversation with a paleobiogeographer one of these days. The relationship between spatial scale and richness, and the relationship between the special pool and the number of observed species in a given set of samples, is a goddamn mess, and we’re never going to explain all of the variance because a some fraction of it is due to effectively random processes. (Guess that’s an oversimplified version of neutral theory in a nutshell?)
A more elegant way of my suggestion about competitive exclusion might not be that competitive exclusion is right or wrong, but that it’s distracting. And all of the theories that have emerged from it might also be distracting from observing a bigger, more central truth that we haven’t realized. Of course, I have no idea what that truth is (and if it were, then I’d probably get offered a position outside my Small Pond and this blog would need someone else to take over.)
Stepping back in an attempt to look at the big picture, do I think that we are going to have some major conceptual breakthroughs that will revolutionize ecology and the ways we understand how organisms interact with the environment? Yes, history tells us that we will be have these breakthroughs.
Do I think that any of these breakthroughs will be forged by mining under the umbrella of the contemporary theories that we are using now? I really don’t think so. There does remain a lot to be learned from observing large-scale and long-term patterns and from doing big experiments related to these patterns. But when someone comes along to revolutionize ecology in a big way that we haven’t seen since the emergence of the discipline, it either will be by showing one of our big ideas is wrong, or by showing that these ideas aren’t relevant to the big picture. As a student of history, that’s just the most likely possibility. We’ll make lots of incremental gains, and I’m glad to be a part of those, but someday one of us will land the big fish. And let’s hope the rest of us will be open-minded enough to see it.
“If what we see in limited cases is caused by mechanisms that do not operate under more common circumstances”
The whole point of the competitive exclusion principle is that it’s a limiting case because it omits mechanisms that operate in nature. That’s how you know what effect those mechanisms have–by looking at what happens when they’re not there.
“I’m of the opinion that attempts to explain high diversity are what gets us in this big mess in the first place. This is a manifestation of the temperate bias that I mentioned. ”
Aha. There’s part of why we’re kind of talking past one another. I agree with you that, from an empirical, what-range-of-local-diversities-do-we-see-in-nature perspective, that’s there’s no reason to take any particular region of the globe as our “baseline” and then say “My goodness, isn’t it amazing that other regions of the globe are so different than that!” But I think the competitive exclusion principle functions as a “baseline” in a different sense. It’s a conceptual baseline, not an empirical one. A limiting case in which the competitive exclusion principle operates would be an important limiting case to consider even in a world in which diversity was the same everywhere, or a world in which academic ecologists were all from the tropics and so thought of high diversity as the “normal” state of affairs, empirically.
“Species richness of a region – the species pool – is simply predicted by speciation rates and extinction rates.”
Fair enough. At one level, the competitive exclusion principle is irrelevant to questions about relative rates of speciation and extinction. It just takes as given that you have some set of species, and asks if they can coexist or not. Though at another level, you could argue that speciation-extinction models always have some sort of implicit ecological assumptions, quite possibly including “sufficiently strong coexistence mechanisms to prevent extinction from happening too fast relative to speciation”. See this old post: https://dynamicecology.wordpress.com/2011/05/02/why-doesnt-community-ecology-erase-the-signal-of-historical-biogeography/
I’m sure we’re each still talking past one another and misunderstanding where the other is coming from rather badly. But I feel like I’m making progress in getting where you’re coming from and I hope you feel the same. I’m enjoying the conversation and finding it very helpful.
I can’t speak to the ecological principles at play here, but that Spinal tap clip…made me laugh out loud. And yes, it is fascinating how we hold onto ideas for so long b/c influential people said them…The geocentric Ptolemeic system, for instance. One thing I’ve learned…there’s always more to a story that the surface and sometimes you come away with new understanding or questions about something. That’s happened to me in my work just this month..excited to set up an experiment to test an idea because of a sudden flash of “Oh, maybe we have this wrong”.
Ever since submitting my master’s thesis to committee, I can’t shake the fear that the topic & approach of my study (social recruitment) are totally irrelevant simply because we know so little about the mechanics of dispersal for volant organisms, particularly migratory ones. We’ve observed a phenomenon that occurs over the briefest period of the organism’s annual cycle, but have no ability to describe or measure the processes responsible for it (prospecting, etc.).
1) I’m starting to abandon the idea that the many phenotypic differences we see among closely related taxa within a radiation have a (measurable) effect on function/selection, that is, they are nearly neutral. Look at the many tens of species of wrasse or damselfish or butterfly fish on a single tropical coral reef. There are slight body shape differences among the species within these families (at least relative to the much larger differences among families). How functionally and selectively meaningful are these differences? I don’t doubt at all that these differences have effects on function and selection, I just think these effects are really really small so the differentiation among species within the clade has a large stochastic component.
This leads directly to the idea that performance/selection surfaces are flattish with many many really small peaks, meaning there are many ways to optimize a certain set of activities. So a specific damselfish, wrasse, and serranid can all basically exploit the same resources on a reef but they all occupy different peaks and so have very different phenotypes. But one isn’t really any better than another in any measurable way.
This then leads directly to the pattern that any particular reef will contain many species of the major families (wrasse, damselfish, butterfly fish, surgeon fish, etc.) but the wrasses for the most part look like wrasses and the damselfish look like damselfish. Even using basic measures like body length:depth. Why does the phenotype group phylogenetically when there has been 10s of millions of years of evolution within these clades? Why don’t the clades really really overlap in phenotype with massive convergence? Sure planktivores might be a little more streamlined within each clade but the planktivores among clades are really different looking. What mechanism is constraining this? David Houle (using drosophila wing shape as the example) has tried to address this and I’m resistant to the path that he is trying to take it but It is a very vexing problem.
2) As an aside, I loved the book Soul Made Flesh by Carl Zimmer
http://www.amazon.com/Soul-Made-Flesh-Discovery-Brain/dp/0743272056
for the same reason you like Dunn. Zimmer does a fabulous job describing how the scientists working on the function of the mind and brain came into it with many deeply held but extremely wrong conceptions of how the body worked and it took a combination of lots of little but brilliant insights and lots of time to exorcise these misconceptions and develop a more modern view of physiology.