A while back we invited you to ask us anything. Today’s question is from Don S, and is paraphrased and modified from the original. Because the original bet Don offered seemed…unattractive. (Sorry Don.) 🙂
What is the least trivial/most profound ecological study or pattern you are willing to attempt to replicate, confident that your replication attempt would succeed?
Jeremy’s answer: I have an old post on betting your beliefs in science. But it doesn’t address your specific question.
My answer would depend on the stakes. The original stakes you suggested–win and you get the satisfaction of winning, lose and you die–would lead me to pick some pattern that’s already extremely well-established, such as “larger areas contain more species”. I’m not staking my life on my prescience! But if the stakes are the sort usually associated with one’s choice of study question, then this gets more interesting. If we rephrase your question as “what is the most interesting or least obvious ‘stylized fact’ that you’re reasonably confident will turn out to be true?”, I’ll go with Bjørnstad’s (2000) observation that large-scale spatial synchrony of cycling populations is lost if those populations stop cycling, due to loss of dispersal-induced phase locking. That generalization is based only on a few toy models and a couple of empirical observations, so it’s very far from being an established fact. And I suspect many people who work on spatial synchrony probably don’t buy it. But I’ll stick my neck out and bet that it’s true. The recent collapse of population cycles in many northern European mammals may provide an opportunity to test my intuition on this. Now that they’ve stopped cycling, they should either lose spatial synchrony entirely (since dispersal no longer has any population cycles to phase lock), or exhibit a very different spatial pattern of synchrony due primarily to the Moran effect. Somebody should totally check this! Unless of course it’s a dumb or infeasible idea for reasons I’m unaware of, in which case forget I ever suggested that. 🙂
I guess I’m going to define this question as “what is the most risky hypothesis you would risk valuable time and energy on because you believe it to be true”. This is quite a bit more risky than ones I would stake my life on (for which I came up with the same answer as Jeremy – larger areas hold more species). Its probably even more risky than Jeremy’s framing as I would say these are likely to be found, not that I am confident they will be found. Here are a couple:
- Many authors over the years have predicted that (at least for birds) population dynamics across an entire range are having some ideal-free-distribution like behaviors (namely individual move from locations that are good but with high population densities to poorer but lower density locations. The evidence that variability is higher in poor sites than high quality sites is quite consistent and suggestive. But nobody has ever found evidence of this. Yet I strongly believe it is true and worth staking research effort on.
- A significant part of the latitudinal gradient in diversity is based not on mean climate but on climate variability. Again this has often been suggested, and I strongly believe it to be true. But it has never moved strongly to the fore as an explanation.
We just published a study suggesting Brian’s #2 is true (climate variation not climate means predicts diversity): https://onlinelibrary.wiley.com/doi/pdf/10.1111/gcb.14375
Thanks for sharing that. Interesting.
Question: why are rates of immigration and extinction so slow? So that climate variation from thousands of years ago still has predictive power for contemporary species distributions? Is this a question lots of people are interested in? I posed in an old blog post (sorry, can’t find it now), but I don’t recall it generating much interest or discussion.
I find the question interesting because it speaks to the cumulative, large-scale, macroecological consequences of small-scale community ecology that happens all the time, everywhere. For instance, one possible answer to the question “why is faunal turnover in response to climate change so slow?” is “it’s a combination of most species having only short-distance dispersal, and local communities having very strong stabilizing mechanisms (sensu Chesson).” Another possible answer (which I highly doubt) is “it’s a combination of most species having only short-distance dispersal, plus all individuals being demographically equivalent so that community dynamics are dominated by slow drift”. And I’m sure there are other possible answers.
I’m not suggesting that we could or should try to infer the strength of stabilizing mechanisms from rates of faunal turnover. I don’t have any specific research program in mind. I’m just a curious outsider, interested to hear from somebody who actually works on this stuff how they think about the connections between small scale community dynamics and large scale macroecological dynamics.
Re: Brian’s #1. This is an interesting one and, I think, a risky one. Many of the flavors of the ideal free distribution basically assume that, at a mechanistic level, animals are making optimal choices when they settle environments. I’m not so sure you would expect a denisty-quality grandient if they individuals only made choices that are “good enough” instead of optimal (even including all the add ons to the theory, eg., despotism, dispersal constraints, ideality is an impossible assumption).
I also think it’s pretty hard to test it without being circular in logic; how do you know the habitat is of high quality without using the locations of the animals?
“I also think it’s pretty hard to test it without being circular in logic; how do you know the habitat is of high quality without using the locations of the animals?”
A bit off topic (but not entirely), this just reminded me of an interaction I had last week, participating on a workshop with mostly animal ecologists. We were discussing habitat quality and how to represent it in the landscape, when someone said the exact same thing “how can I know if a place is high quality without knowing where the inviduals are first?”.
And at that moment it dawned on me how much the brains of animal ecologists and plant ecologists are wired differently. For plants, we tend to think mechanistically when thinking about habitat quality (water/light/carbon use efficiencies and adaptations/requirements to increase them). Heck, we can start with stomatal conductances and carboxylation rates, and scale up reasonably all the way to biome, thinking mechanistically the entire way. But animal ecologists are much more empirical; distributions and abundances come first, and then inferences about requirements follow (maybe because of movement plus behavioral plasticity?). Of course, there are lots of empirical and mechanistic studies on both camps, but is was funny to notice how the “default” way of thinking is fundamentally different between fields.
That’s a super interesting observation and I think spot on. As an animal movement ecologist myself I try to think about how to get evidence about those mechanistic-scale processes given that what we have often are the “emergent-scale” data sets (i.e., movement/location data). There are statistical techniques but it seems like they often just recover researcher expectations. There are ways to go about it (I think) but you’re right – it’s working backwards instead of from the first principles that give rise to the phenomenon.
Jeremy, I mainly agree with your statement about spatial synchrony. I wonder if you could do a microcosm experiment that would test this explicitly? One thing that I’ve found a bit disappointing about using historical data for inference into this phenomenon is that it seems like lots of things change besides just whether the populations are cycling.
I’ve done it. See Vasseur and Fox 2009 Nature.
Good point, although I was envisioning starting with a group of cycling populations and then doing something to stop the cycling in those same populations, which is a bit different from the design of Vasseur & Fox 2009. Probably not different enough to change any conclusions, though.
Ah, ok, I see what you mean. Hard to figure out a feasible way to do that experiment. Since you gave me the opening, I will now bore you with technical remarks about protist microcosms. 🙂
-Removing all the predators to stop the prey from cycling would require pulling them out one by one with a micropipet, which would take approximately forever. And as you say, that would almost certainly just give you the same results as Vasseur & Fox 2009 anyway.
-I suppose you could try thickening the medium with methyl cellulose to reduce the predator-prey encounter rate, a la Luckinbill’s work in the ’70s (Harrison 1995 Ecology is a great reanalysis of Luckinbill’s data). But I played around with that during my postdoc, and couldn’t get it to work. It’s an extremely finicky method. There’s a sharp threshold between “not enough thickening to make any difference” and “too much thickening; the protists can’t move and the predators all starve to death”.
-Only thing I can think of that *might* work would be to start with high enrichment cultures containing many wheat seeds. Pull out all the wheat seeds to convert them into low enrichment cultures, thereby hopefully stopping the cycling.