My collaborators and I just published “Population extinctions can increase metapopulation persistence“. New Scientist did a piece on it, which is the first time any media outlet other than my local newspaper has written up my work. I’m chuffed about this, because I think this is the coolest paper I’ve ever done by some distance.
Or, maybe it’s just a cute result–a fun curiosity. I could even imagine someone arguing that it’s oversold fluff. So why do I think it’s so cool? And what’s the difference between “cool” and “cute”?
Here’s the gist of the paper (the core of which I spoke about at ESA a couple of years ago). The paper’s about what we’re calling “the spatial hydra effect” on metapopulation persistence. In Greek mythology, the hydra is a multi-headed monster that grows two new heads every time one is cut off. It’s the ultimate example of the old saying that that which does not kill you makes you stronger. Peter Abrams coined the term “hydra effect” to refer to situations in which increasing a population’s mortality rate increases its abundance. Our paper is about a spatial hydra effect that arises for reasons unrelated to those Abrams considered. When you have a spatial hydra effect, population extinctions actually increase metapopulation persistence rather than reducing it. They do this because they’re desynchronizing. It’s well known that metapopulation persistence depends on sufficient asynchrony. If all populations crash at once, there’s no source remaining for recolonization (or for a rescue effect to prevent local extinctions). The spatial hydra effect arises because local extinctions (say, due to a severe local disturbance) can be very desynchronizing; they’re like especially severe perturbations to the local population’s abundance. A population that goes extinct and then later gets recolonized isn’t likely to be in sync with the surrounding populations, even if it was in sync with them pre-extinction. The resulting asynchrony ensures that extinct populations quickly get recolonized by emigrants from other currently-abundant populations. It’s an irony: on the one hand local extinctions create extinction risk for the entire metapopulation–but on the other hand they create the asynchrony that metapopulations need to persist.
Put another way, the optimal rate of local extinction for many metapopulations is an intermediate rate, not a low rate. If the local extinction rate is too high, populations go extinct faster than they can be recolonized and the metapopulation doesn’t last long. But if the local extinction rate is too low, the metapopulation doesn’t last long because all populations will sync up and then crash at once.
In our new paper, we show that the spatial hydra effect increases metapopulation persistence in three different stochastic metapopulation models (a single-species model, a host-parasitoid model, and a predator-prey model), and in experimental predator-prey metapopulations in laboratory microcosms. So it’s a generic effect that operates independent of many system-specific ecological details. And it’s not a subtle effect: raising the local population extinction rate can increase expected metapopulation persistence time by 50%, 100%, or even 1000% depending on the ecological details. The key precondition for the spatial hydra effect is local population cycles that can be spatially-synchronized (“phase locked”) by dispersal. Which, ok, isn’t the most common population dynamic in the world. But there are species we care about exhibit periodic outbreaks that can be synchronized by dispersal, including both species of conservation concern and terrible human diseases. See our paper for discussion of possible natural examples of the spatial hydra effect.
I think this result is extraordinarily cool, even profound.* It’s a great example of a “double-edged sword“, a situation in which a single cause (here, population extinctions) necessarily has two opposing effects (here, on metapopulation extinction risk), and interest centers on the relative magnitudes of those two effects. It’s also a great example of a result that’s counterintuitive until you think about it–and then it becomes intuitive. Results that replace our old intuitions about how the world works with better intuitions are some of the most important results, I think. I also think it’s cool because it’s a result that was kind of hiding in plain sight. We found the spatial hydra effect using bog standard, simple theoretical models that have been well-studied before. You might think there wouldn’t be anything left to learn about the behavior of simple metapopulation models–but you’d be wrong. I’m also proud of the way we demonstrated the result; I think we did a good job of combining theory and experiment, and of demonstrating the generality of the result. I also think we did a good job taking full advantage of the power of our model system; I doubt an experimental result this clean could’ve been obtained outside microcosms. And like any good result it raises interesting new questions. One of the biggest is whether the spatial hydra effect also works with endogenously-generated local extinctions, as opposed to extinctions due to exogenous disturbances. Think of local extinctions due to demographic stochasticity, or of local population cycles crashing to extinction of their own volition, as when a disease outbreak exhausts all the susceptible hosts in the local population and so burns itself out. If the spatial hydra effect works with endogenous extinctions too, then that broadens the range of natural systems in which we might expect a spatial hydra effect to operate. A spatial hydra effect that operates with endogenous extinctions would also just be the ultimate irony, because it would mean that the metapopulation itself generates the local extinctions that it needs in order to persist via asynchronous colonization-extinction dynamics.
But on the other hand, I wouldn’t blame you if you thought this was more “cute” than cool. If you don’t care about intuition and conceptual understanding, say because you only care about prediction, you won’t care that the spatial hydra effect sharpens our intuitions about metapopulation dynamics. If you think the only important task of ecology is to provide management advice for specific natural systems, then you’re going to think our new paper is as unimportant as any other bit of fundamental ecological research. If you’re the sort of person who thinks that a phenomenon isn’t interesting or important until it’s been shown to operate in nature, then you’re not going to be very impressed with our paper. If you’re the sort of person who thinks that a phenomenon isn’t interesting or important until it’s been shown to be common and strong in nature, you’re definitely not going to be very impressed with our paper! After all, most populations don’t cycle, metapopulations maintained by colonization-extinction dynamics don’t seem to be all that common, there are lots of things that affect metapopulation persistence besides the spatial hydra effect, and as far as I know there aren’t any natural examples of entire metapopulations that have gone extinct because the local populations all phase-locked and then crashed at once. If you’re the sort of person who thinks that multicausality is what makes ecology both challenging and fun (hi Brian!), you’re probably not going to be too excited about a highly-controlled experiment designed to isolate one determinant of metapopulation persistence among many. And if you’re the sort of person who thinks that describing and explaining large-scale patterns is what ecology is all about (hi Jim!), because the alternative is disappearing down a rabbit hole of reductionist research that festishizes internal validity, you’re not going to be very excited about a process-first (rather than pattern-first) research project based on laboratory microcosms.
I disagree with all of the views sketched (and hopefully not caricatured) in the previous paragraph. In particular, I disagree with the view that the only phenomena that are really worth caring about are those that are common and strong in nature.** But every view in the previous paragraph is defensible. Professional judgments about what research is most interesting or important or etc. are just that–judgments. They’re partially subjective, but also partially objective. They’re based partially on purely-personal preferences, but also partially on cogent reasons that other professionals can appreciate if not necessarily agree with. And we can’t do without such professional judgments, except at the cost of ecology ceasing to exist as a professional discipline.
So purely to indulge my own curiosity, here’s a little poll: how cool and interesting do you think our spatial hydra effect paper is on a scale of 1-10? Where 1 is “trivial, oversold rubbish”, 5 is a typical paper in a mid-level ecology journal, and 10 is “I would nominate this paper for the Mercer Award if you were still eligible, Jeremy.” As this post hopefully makes clear, you won’t hurt my feelings no matter how you vote, so be honest. 🙂
*Which is why we originally submitted to Nature, where the paper was reviewed, revised, and ultimately rejected. Which was disappointing, but fine. The ms was considered fully and fairly by the reviewers, which is all any author can ever ask.
**In part because the definitions of “common” and “strong” are unclear. For instance, bacteria, archaea, and viruses vastly outnumber macroscopic organisms. Does that mean that everybody except microbial ecologists studies organisms that are “rare” or “unusual” and therefore comparatively uninteresting or unimportant? As another example, human beings surely have stronger effects on the planet than any other species, by any plausible measure. Does that mean any ecologist who studies anything other than anthropogenic impacts is studying unimportant phenomena?
Well I definitely like your article rating scale. When finishing a review, and the going to turn it in and the journal website asks for a 1-10 rating, wouldn’t it be refreshing to have such straightforward definitions? Something like “Dear Reviewer, in addition to your detailed review please rate the submission on a scale of 1 to 10, where where 1 is “trivial, oversold rubbish”, 5 is a typical paper in a mid-level ecology journal, and a 10 is “contender for most interesting paper of the year.”
+ Overly honest review recommendations? If I were EIC….
Peer review service Rubriq already provides something like this, except they use three 1-10 scales rather than just one (quality of research, quality of presentation, novelty/interest). https://www.researchsquare.com/publishers/rubriq. Although as far as I know they don’t link those scales with my overly-honest definitions. 🙂
And there’s a guy in statistics who’s come up with a Tinder-style app for post-publication review of arXiv preprints. Swipe in one direction if you liked it, swipe in the other direction if you didn’t. Oh brave new world…
I promise that the one person who already gave our spatial hydra effect paper a “10” is not me. 🙂 Even I wouldn’t score it quite that high.
So far nobody’s scored it below a 5, which doesn’t surprise me. Our readership is probably self-selected to like the same sort of science Meghan, Brian, and I like. And the post’s teasing of Brian aside, he doesn’t actually dislike this sort of paper.
Update: we now have a vote for “trivial, oversold rubbish”.
As more votes come in I’ll be curious to see the overall distribution. Will it have a single mode, or will there be multiple modes, perhaps suggesting a “lumpy” distribution of our readers’ preferences for different sorts of work? Early voting suggests the possibility of a trimodal distribution. One mode around 7-8, indicating readers who share my own feelings about the paper. One mode at 5, indicating readers who think of the paper as a typical mid-level ecology paper. I’d expect many readers who don’t know anything about the paper besides what I said about it in this blog post to give it a 5. And perhaps we’ll see development of a small mode at 1.
And now with 97 votes in, it’s looking like either a unimodal distribution with a peak at 7-8, or a bimodal distribution with a second, smaller peak at 2-3, depending on whether you think the paucity of votes for 4 is real or just a blip.
I didn’t know anything about the paper besides what you said about it in this blog post and I gave a 9 after reading the paper, even though I’m not specialist in this field.
1- I always like learning stuffs, epecially when I’m not a specialist.
2- I also like reading stories. Obviously, science quality must be good (and the results robust). But a good paper isn’t always the paper which presents the most innovative results (even if this helps). Here, the paper is well-written and clear for the readers.
3- Even if I’m not a specialist of these questions, I can feel the novelty and this is quite important to reach the top. I think that if the audience understand the conclusions (and more importantly if you understand your audience!), then the paper makes a great contribution in Ecology (and not only in your field).
First time I leave a comment on this blog, but I wanted to contribute by saying that some non-specialists (like me) appreciate the work of other people in other disciplines as long as this is accessible. Great job!
Thanks for the very kind words Nico.
Makes me think of Richard Levins view of mathematical theory: “I have always enjoyed mathematics and see one of its tasks as making the obscure obvious. I regularly employ a sort of mid-level math in unconventional ways to promote understanding more than prediction.”
That’s a great line about making the obscure obvious! Thanks for sharing.
I think that multicausality is what makes ecology both challenging and fun and I usually get very excited about highly-controlled experiments designed to isolate one or few of those causes. Most of the beauty of multicausality comes from comparing how nature would be if it was driven by a single process, and how nature really is.
Very interesting comment! I’m now very curious to hear if Brian and others who like multicausality would say the same.
Absolutely. To me multicausality lays out a two step program:
1) Study each cause in isolation to fully understand it
2) Figure out what determines which processes are important under a given context
I personally may be a bit more interested in #2 (and I might argue that ecology has tended to underemphasize #2 relative to #1 to its detriment) but they go hand-in-hand and I am glad people pursue #1
I’m curious whether you explicitly developed your models (and subsequent experiment) to test the spatial hydra hypothesis or you rather developed models to predict “…the effects of dispersal rate and local extinctions on metapopulation persistence…” and a result in support of the hypothesis came as a surprise? I don’t think the answer has any bearing on the strength of the paper – which I think is very interesting, btw – only that I’m curious in a general sense how often the hypothesis–>model/experiment–>result in support of the hypothesis narrative actually reflects what was done. Did you have to find a hypothesis to support your result rather than the other way around?
The genesis of the hypothesis was my own non-mathematical intuition. I was puzzled by the apparent tension between two well-known features of metapopulation dynamics of cycling species. 1. Cycles are easily spatially-synchronized by even low rates of dispersal (e.g., Vasseur et al. 2009, Fox et al. 2013). 2. At intermediate dispersal rates metapopulations exhibit asynchronous colonization-extinction dynamics. Which is puzzling: in light of #1, how is #2 possible? Why isn’t any rate of dispersal high enough to generate an appreciable rate of recolonization not also high enough to produce spatial synchrony? The answer, or at least an answer, is local extinctions and their desynchronizing effects. Low rates of dispersal easily spatially-synchronize local population cycles only when those cycles are persistent locally.
The mathematical models were a test of that intuition, and they turned out to confirm it. Then we did the experiment, and that turned out to confirm the intuition as well.
So yes, in this case the hypothesis–>models/experiments–>results narrative reflects what was actually done.
I’m actually shocked that my pre-mathematical intuition turned out to be correct, at least in the case of local extinctions due to exogenous disturbances. The models and experiments were tests, not demonstrations. They weren’t “rigged” or “designed” to exhibit a spatial hydra effect. We just set up models and an experiment in which we could vary both the dispersal rate and the local extinction rate, and then discovered that those manipulations generated the spatial hydra effect predicted by my pre-mathematical intuition.
Whether the spatial hydra effect also works with endogenous local extinctions remains to be seen. So far, it seems like the answer is “sometimes yes, sometimes no”. In general, endogenous extinctions appear to be less desynchronizing than exogenous ones that could happen at any time, and so don’t generate as strong a spatial hydra effect. But it’s still early days on that front.
Question: does the fact that this paper–or indeed, any paper–inspires such a wide spread of opinion among ecologists a bad sign for the field as a whole? As of this writing, there are a couple of people who think it might be the paper of the year, and three who think it’s trivial, oversold rubbish (or nearly that bad). Both minority opinions, obviously–but is the fact that they exist at all a bad sign? A sign that ecology is not a coherent discipline at all, but just a bunch of people with different subjective opinions who happen to work on vaguely-related things?
Or maybe it’s not a bad sign, because perhaps a typical paper in any discipline (physics, cell biology, economics, sociology, you name it) usually inspires the full range of possible reactions, from “this is trendy, oversold rubbish” to “this is the paper of the year”? So that the fact that a few people love any given paper, and a few people hate it, doesn’t signal lack of disciplinary coherence?
Or maybe it’s only rare papers that inspire a wide range of reactions, and those are the most interesting papers in any discipline? I’m recalling someone (Peter Medawar?) saying that the most important papers are those that some reviewers love and others hate. Because any paper that doesn’t inspire a wide-range of strong reactions is probably boring.
And of course, it’s also possible that some or all of the people who scored the paper a 10, or a 1 or a 2, are just trolling. And more broadly, I doubt that most of the poll respondents are giving very considered opinions based on careful reads of the paper. Most people probably just completed the poll based on an off the cuff reaction to my blog post. The off the cuff reactions of only-barely-informed people probably shouldn’t be taken too seriously. (Except of course that that’s what a lot of collective opinion about a lot of scientific topics amounts too. Scientists form casual opinions about scientific topics all the time, based on little more than having heard a talk on the topic, or read a couple of abstracts on the topic, or etc. It’s interesting to ask whether those casual opinions shape the direction of science in any important way…)
I have often wondered the same thing, and was prompted to do so again recently by a molecular-biologist colleague. I am about to start serving on the NSERC Discovery panel, and he had done so as well in the past (different subject area) but sometimes was called upon to give input on a proposal in the eco-evo panel (presumably something molecular). His first comment was “you guys are mean!”. Digging a bit deeper, the distinction he was drawing is that in other disciplines it seems people criticize _how_ science is/was done (e.g., are the methods appropriate to the question), whereas ecologists criticize why someone would even do the thing they’re proposing to do. To me, that’s a sign that we lack coherence as a discipline in terms of not even agreeing on what constitutes something worth pursuing. (And it wasn’t just comparing two disciplines – he had been called into other groups as well.) Food for thought at least…
Very interesting. Seems like good fodder for a post. Want to write one? It could be a short discussion-starter.
I know of several instances where people were told by colleagues “if you publish this you’ll ruin your career”. It didn’t happen in any of the cases. IMO it should be more or less normal because strongly dissenting views should generate more challenges or replication efforts testing the result, strengthening science as a whole.
Presumably those papers challenged established dogma? I agree that, in general, people tend to overrate the possibility that writing controversial papers (or papers that some bigwig just doesn’t like) will hurt their careers:
Our spatial hydra effect paper doesn’t challenge any established dogma as far as I’m aware, so we didn’t have to worry about that. I presume that the poll respondents who don’t like it don’t like it because they think it’s boring or unimportant or oversold. Not because they see it as challenging established dogma or as an attack on their own pet ideas.
Yes the cases in thinking about were dogma crashers. But that needn’t be the case for strong differences of opinion, which again I think good for science. Polite applause is the worst possible reception. FYI though I did not vote in the poll, my opinion on your paper is 7ish
Hi Jeremy – your post raises a few comments/questions in my mind:
1. I scored the paper 7 but not because I read the paper, but because I read your pitch of what the paper was about and why you thought it was important, and you make a convincing argument [I guess that makes me “only-barely-informed”…. :-)]. Without this post I’d be very unlikely to have looked at the paper – I find it impossible to keep up with the literature in my immediate field – so reading your summary was a great introduction to it. But I clearly remember a post of yours from some time ago in which you discussed what DE was and was not going to cover. One of the things you weren’t going to cover was announcements/summaries of your own research papers. Is this a change of policy for DE? If so then I’m all in favour of it because I think that popularising/promoting your own science _to other scientists_ is an important part of blogging. Although I probably won;t ever cite your paper I feel (intellectually) richer for knowing that it exists and for having read your summary, so that’s a good thing.
2. Now a question about the work itself. In your models your tested two antagonistic (+-) species interactions (predator-prey and host-parasitoid). Why did you not test mutualistic (++) or commensal (+0) models? Is that possible to do? And would your results have changed if you had?
3. Finally, I’m going to challenge one of your throw away comments: “human beings surely have stronger effects on the planet than any other species, by any plausible measure”. I’d make a case for the cyanobacterium _Prochlorococcus marinus _, which is estimated to be responsible for 30-80% of open ocean primary productivity, 20% of global oxygen production, and 25% of global CO2 sequestration: https://en.wikipedia.org/wiki/Prochlorococcus
“One of the things you weren’t going to cover was announcements/summaries of your own research papers. Is this a change of policy for DE?”
I’d say it’s a one-time stretching of the policy. I wanted to do a post on how the same paper can seem cool to some and not cool to others, and decided to use one of my own papers as a case study.
I’ll confess to also wanting to get the word out about this paper, because it appears in a new journal to which few will have access. But I don’t plan to make a habit of that.
Re: 2, one of our theoretical models is a single-species model with a time lag. And we now have another model we didn’t publish, a model of an “integrate and fire” oscillator (the sort of model often used to model synchrony of neuronal firing), in which the spatial hydra effect works. So it’s not that we *only* tested (+,-) interactions. But yes, two of the models and the experiment were (+,-) interactions. That’s because they can generate population cycles. It actually doesn’t matter what underlying mechanism generates the population cycles, so if you could gin up a (+,+) interaction model that generates regular cycles, the spatial hydra effect mechanism would still operate. Or else a model that just happens to have a (+,+) interaction, but in which the cycles are generated by a time lag or by some other interactions.
Re: 3, I was wondering if commenters would start debating whether humans actually are the species with the “strongest” effect on the planet. Thereby illustrating my point about how all such claims are fairly arbitrary. 🙂
“it appears in a new journal to which few will have access”
Unfortunately you are correct … no access, so cannot comment. Maybe you can post a pre-print? Or use one of the share services such as Researchgate?
Please encourage accessible publishing practices (especially when you are keen to hear what we think!).
Congratulations in any case!
I don’t have a pdf, sorry. Nor do my co-authors. The link in the post goes to a public read-only full text version.
“The link in the post goes to a public read-only full text version.”
Unfortunately, that must be location specific. No full text available from here.
Jeff – I’m going to have to go with Jeremy on humans.
50% of all the nitrogen fixation on the planet. 50% of the land surface area modified. 50% of all freshwater appropriated. 40% of the land NPP (25% of global NPP). While I do appreciate prochlorococcus role in the oxygen I breathe, I’m still going to have to go with humans.
All true, Brian, but 70% of the planet is open ocean! Prochlorococcus has a massive role to play as the basis of a food chain that ultimately feeds 100s of millions of people. Plus without the 25% of global annual CO2 sequestration we’d be in trouble.
As Jeremy notes, any such assessment is fairly arbitrary, though I can’t think of any other single species that has as much impact as humans or Prochlorococcus, so whichever way it goes, they rank first and second 🙂
One other reason I’m proud of this paper: I think it’s one of the best-written papers I’ve ever done. The whole “hydra” analogy isn’t just (or even primarily) salesmanship. Rather, the analogy helps readers understand the central result, as opposed to convincing them the central result is interesting. At least, that’s the intent; I’d welcome comments from readers as to whether the hydra analogy aided their understanding of the paper.
When I read “Spatial hydra effect”, I expected something a little different out of two reasons:
1) I associate hydra with something growing bigger and stronger or increasing in abundance
2) Often Hydra is something that you refer to that it is better to left alone otherwise the issue becomes to larger
In your analogy, it is about persistence and not about “getting bigger” (if I did not miss something). Which does not fully fit with my expectations and thus did not really help understand the paper. But in the end I like the analogy and I think it fits, but not with my first expectations.
But did you consider that one head of the Hydra was immortal? 😉
Re: 1, the mythical hydra only does that when it loses a head.
In our analogy, what “gets bigger” when local extinctions occur is the recolonization rate.
And yes, the fact that the hydra is immortal by virtue of its ability to grow two new heads every time one is cut off is analogous to how the spatial hydra effect increases metapopulation persistence. 🙂
First two sentences of the abstract sound exactly like Brown’s “rescue effect” which isn’t even cited. Am I missing something? OK different model but same principle.
No, the spatial hydra effect is not the same as the rescue effect. With a rescue effect, dispersal prevents extinctions that would otherwise have occurred. Here, local extinctions occur, but because of the resulting asynchrony, recolonization events occur more rapidly than they otherwise would.
Possibly, some of the increased persistence generated by the spatial hydra effect could be because asynchrony also increases the strength of rescue effects, preventing some local extinctions that would otherwise have occurred.
(Aside: the first two sentences of the abstract are a summary of already-known background information. Our new contribution is stated in the third sentence of the abstract.)
Brown and Kodric-Brown were cited in a previous version, but we were over the reference limit for Nature and had to axe some references. I don’t like reference limits and don’t really see the point of them in this day and age of electronic publication.
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