What are the biggest puzzles in ecology?

A scientific puzzle is anything that’s true without any obvious reason for it to be true, especially if there’s some obvious reason for it not to be true. Resolving scientific puzzles often leads to deep and important insights.

Evolutionary biology is full of puzzles, most of which have the form “Evolution by natural selection should produce X but yet we see Y. How come?” Examples include the surprisingly high frequency of sterile males, individuals that help unrelated individuals reproduce, and senescence. Resolving the puzzle usually involves figuring out why trait or behavior X actually is adaptive despite appearances to the contrary, as with individuals that help non-relatives reproduce. Or else why natural selection can’t purge it, as with senescence. Other classic puzzles in evolutionary biology include how complex adaptations like the human eye could evolve via small, piecemeal steps, and why there are usually only two sexes.

What are the biggest puzzles in ecology? Does ecology have as many puzzles as evolutionary biology? And if not, does that indicate a failing of ecology?

Here’s a classic ecological puzzle: Hairston, Smith, and Slobodkin’s question, why is the world green? That is, why is the world covered with plants, given that there are lots of herbivores around that you’d think would eat all the plants?

Here’s a recent ecological puzzle I’m intrigued by: why is the productivity of an assemblage (i.e. the amount of new biomass it produces per unit time) a power law function of its biomass with a slope of 0.75? (Hatton et al. 2015) Why should it be a power law relationship as opposed to a straight line or an exponential or whatever? And why should the exponent usually be 0.75 rather than some other number? This one’s especially puzzling because the most obvious explanation–“it has to do with the 3/4 power law scaling of metabolic rate and body size”–can be ruled out.

Those two ecological puzzles are what Mark Vellend calls “global” puzzles: puzzles about a common feature of many different systems. Here’s a more “local” ecological puzzle. I recently published a paper that solves a puzzle that had been bugging me. The puzzle is the apparent contradiction between two facts about metapopulation dynamics in the case where population dynamics are cyclic, as with outbreaking diseases. On the one hand, metapopulation persistence is maximized by intermediate rates of dispersal among populations. Intermediate rates of dispersal provide rapid recolonization of local populations that go extinct, but not so much dispersal that population cycles in different patches synchronize, creating the risk of all populations crashing to extinction at once. On the other hand, when local population dynamics are cyclic, we know that even very low rates of dispersal among populations synchronize their dynamics. So how is it possible that there could be intermediate rates of dispersal that aren’t synchronizing? The resolution of the puzzle is that local extinctions are desynchronizing. You need them to happen often enough keep the population cycles from syncing up, but don’t want them to happen too often because then recolonization wouldn’t be able to keep up. That is, what maximizes metapopulation persistence in the cases where local population dynamics are cyclic isn’t an intermediate rate of dispersal, but an intermediate ratio of dispersal rate to local extinction rate. Very low rates of dispersal are synchronizing only when local extinction rate is zero or extremely low. As I said, this is only a “local” puzzle, but I think it was big enough to be worth thinking about, and it’s satisfying to have solved it.

So, what do you think are the biggest puzzles in ecology? Is there a local puzzle about your own system that you want to solve? Is ecology short on puzzles compared to evolutionary biology, and if so, is that a problem? Tell us in the comments!

26 thoughts on “What are the biggest puzzles in ecology?

  1. Why do labrids look like labrids and pomacentrids look like pomacentrids and acanthurids look like acanthurids? These are three different families of reef fishes that share both a similar swimming mechanism (they swim using pectoral fin oscillation and not body undulation) and habitat and yes they all co-occur in abundance on any reef. By “look like” I mean that members of the family barely overlap on a simple scatter plot of body shape (relative depth of the body vs. relative width of the body). The families are many 10s of millions of years old so I’m pretty sure any sort of Lande or Lynch or Bookstein like diffusion model of body shape evolution would allow each family to completely fill the phenotypic space. The answer might be ecological – there is too much competition in whatever the niche is that is optimized (not sure this is the right word) by the pomacentrid body. Or the answer might be developmental/genetic – there are developmental/genetic “constraints” (is there really too little genetic variation in the direction of the pomacentrid mass for labrids to evolve much in this direction?). And, is the answer general or specific to every case (each unhappy family is unhappy in its own way)?

    This question is inspired by Hansen and Houle’s broader question in Hansen, Thomas F., and D. A. V. I. D. Houle. “Evolvability, stabilizing selection, and the problem of stasis.” Phenotypic integration: studying the ecology and evolution of complex phenotypes. Oxford University Press, Oxford (2004): 130-150.

      • Excellent – I haven’t seen that. I bet the answers Tilman explored differed radically from those that Hansen and Houle explored.

      • Clumping vs. smeared helps to rephrase an ecological pursuit of the question. Is the labrid clump due to
        1) the morphospace around the labrid clump isn’t a good solution to any ecological problem (so there are no species smeared across the space)
        2) the morphospace around the labrid clump is already occupied by a superior competitor (there are species smeared across the space just not labrid species)

        This raises the question, if pomacentrids (on one side of labrids in the phenotypic space) and acanthurids (on the other side of labrids) didn’t exist, would labrids be smeared across the space?

      • I agree the clump/schmear is an important one. I knew somebody at UA who found this same phenomenon in asexually reproducing bacteria along a temperature gradient. So its got to be something about adaptive landscapes. But mostly ecologists seem to think this is an evolutionary question and evolutionists think this is an ecological question

      • “But mostly ecologists seem to think this is an evolutionary question and evolutionists think this is an ecological question.” Great point. It’d be interesting to come up with a list of questions where people think like that.

  2. Understanding the processes behind the latitudinal gradient in diversity (or more properly why diversity covaries with climate at global scales).

    Understanding what traits/phenotypes/contingent histories make a species common or rare. We have surprisingly little traction on this. A few hints about frequency dependence and soil pathogens, but those are not direct answers to the question.

    • Re: the latitudinal diversity gradient, there’s been some recent progress on that: https://dynamicecology.wordpress.com/2017/10/05/what-papers-should-be-considered-for-the-2018-george-mercer-award/.

      I agree with you that linking traits/phenotypes to abundance is a puzzle. I think that’s because you need to think about density and frequency dependence when you’re thinking about abundance. But the mapping from species’ traits to density and frequency dependence often isn’t straightforward, even in contrived simple scenarios where it seems like it ought to be straightforward. My own modest effort on this front: https://dynamicecology.wordpress.com/2011/05/19/when-should-species-traits-predict-species-abundances/

      • LaManna et al is a good paper. But I’d hardly say its cracked the nut on the latitudinal gradient. I very much doubt any one paper will. Density dependence is still pretty phenomenological. And the links to climate (which is a better phrasing than latitude) are still pretty open.

      • Have a look at Usinowicz et al. I’m still not *totally* convinced by the model fitting. But they’ve got a fairly convincing mechanistic story underpinning their results. Basically, the longer growing season in the tropics means there’s more scope for different tree species to reproduce at different times under different environmental conditions, leading to a stronger storage effect in the tropics. Which if so is *really* interesting, because it means that environmental fluctuations are actually more important to diversity maintenance in the tropics than in temperate or polar regions.

      • I’ve only had time to skim Usinowicz so far. Its in my pile to read more closely.

        I also think the role of seasonality is underappreciated

        But to really crack the latitudinal gradient, you have to have a mechanism general enough to explain gradients in marine bivalves in the Mesozoic (e.g. Powell 2007).

        That’s not a knock on any paper. More a musing on what a solution to a big problem looks like – should we expect one big explanation – or is several smaller explanations more likely.

      • Yes, the Usinowicz et al. mechanism is specific to tropical trees.

        Re: big problems with one big explanation vs. several small explanations, I wonder if part of the reason the latitudinal diversity gradient is so tough to crack is because it’s one of the rare problems that looks like it should have one big explanation but in fact has a bunch of small ones. It’s such a general pattern across so many taxonomic groups, and has held for so long, that it sure *seems* like it ought to have one overarching explanation that applies to all taxonomic groups at all times. But maybe it’s just a coincidence that various different explanations at work for different taxonomic groups at different times all just so happen to generate the same pattern. I don’t know, obviously! Just musing.

        There is some precedent for this sort of thing in science. Think of how estimates of the age of the earth in Darwin’s day all gave numbers in the same ballpark despite being based on totally independent considerations. Which strongly suggests that those estimates were all correct–but they weren’t. By a very unlucky coincidence, estimates that were totally wrong for totally different reasons all just so happened to give similar wrong answers.

    • Similar to your comments above on ecological versus evolutionary drivers — to me, the more compelling explanations for the LDG (or lack thereof) are all macroevolutionary rather than contemporary. While storage effects and negative density dependence seem likely candidates for maintaining the standing LDG for trees these explanations aren’t (yet) satisfactory for explaining the LDG’s origins nor its prevalence across the tree of life. Instead, the roles of long-term regional stability, large areas, and productivity seem like intuitive, attractive explanations for the establishment of diversity gradients at the global scale and are easier to reconcile with groups that don’t show LDG’s. Just my 2¢!

    • Can you put this puzzle in the “We see X but expect Y” framework? Or are we so far behind at understanding processes behind latitudinal gradient diversity that it’s not so clear what X and Y are. In some ways puzzles of the form “We see X but expect Y” are often much further along than many fascinating open research questions where X and Y aren’t so well understood (especially Y).

      • On the other hand, not having any idea what to expect is a precondition for mistakenly *thinking* that you know what to expect. Which is a recipe for spinning your wheels, trying to solve a “puzzle” that’s actually a non-puzzle.

        Part of the problem with, say, the intermediate disturbance hypothesis is that lots of people thought they had good reason to expect a hump-shaped diversity-disturbance relationship when in fact they didn’t. Peter Abrams has an old Ecology paper arguing the same was true for humped diversity-productivity relationships. There was actually no good theoretical reason to expect any particular relationship between those two variables. So there’s no “puzzle” about why some “weird” systems don’t exhibit humped diversity-productivity curves–because there’s actually nothing weird about those systems, no theoretical “rule” to which they’re the “exception”. Local-regional richness relationships are a third example. The notion that they should be linear when local species interactions are weak and saturating when they’re strong is wrong. Theoretically, there’s no particular reason to expect any particular local-regional richness relationship. So there’s nothing puzzling about the fact that ~half of observed relationships are linear and half are saturating.

    • >But to really crack the latitudinal gradient, you have to have a mechanism general enough to explain gradients in marine bivalves in the Mesozoic (e.g. Powell 2007).

      Edgar et al just published an interesting paper in Science Advances that might be of interest:

      Among the most enduring ecological challenges is an integrated theory explaining the latitudinal biodiversity gradient, including discrepancies observed at different spatial scales. Analysis of Reef Life Survey data for 4127 marine species at 2406 coral and rocky sites worldwide confirms that the total ecoregion richness peaks in low latitudes, near +15°N and −15°S. However, although richness at survey sites is maximal near
      the equator for vertebrates, it peaks at high latitudes for large mobile invertebrates. Site richness for different groups is dependent on abundance, which is in turn correlated with temperature for fishes and nutrients for macroinvertebrates. We suggest that temperature-mediated fish predation and herbivory have constrained mobile macroinvertebrate diversity at the site scale across the tropics. Conversely, at the ecoregion scale, richness responds positively to coral reef area, highlighting potentially huge global biodiversity losses with coral decline. Improved conservation outcomes require management frameworks, informed by hierarchical monitoring, that cover differing site- and regional-scale processes across diverse taxa, including attention to invertebrate species, which appear disproportionately threatened by warming seas.

      Edgar et al., Sci. Adv. 2017;3: e1700419

  3. And geographic ranges. We have no clue what really sets those. Climate is in the mix somehow. But clearly only part of the mix, and transplants outside of a range are usually successful. So what gives?

    • I think this is one is going to fall on the “several small” side of the “one big vs. several small explanations” gradient. I’m curious- what are the definitions of “usually” and “successful” with regard to the success of transplants? Does success mean populations are established? I haven’t read that much evaluating the success of transplants, so I’d appreciate suggestions of papers to look at!

      • For an excellent review of the literature on transplant experiments and what they tell us about the determinants of species’ range limits, check out Hargreaves et al. 2013 Am Nat.

        Note that there’s another slightly more recent review of this same literature, but the Hargreaves et al. review is much stronger in my view.

    • Climate terrane and competition?

      I mean, if you start at Red Lake Ontario you could walk NW around lake Winnipeg and all the way across Saskatchewan and hardly change species assemblages, right? But go less than half the distance from the Hoh River mouth (on WA state coast) to Spokane, WA, and you’ll pass through (guessing) 20 or more species assems as you go from rain forest to mountain peaks to deserts. Right?

      I guess I’m missing something…

  4. One puzzle that intrigues my students and I is: why is the relationship between specialization and abundance in a given species sometimes positive (niche breadth hypothesis) and other times negative (trade-off hypothesis)? We have been working to solve this puzzle in the past years, using interaction networks as a model, which has been really fun. Last year, we proposed a first step towards a possible solution: https://doi.org/10.1016/j.ijpara.2015.10.002.

  5. I think this is a great use of the blog platform and look forward to reading comments.
    Regarding your question “why is the productivity of an assemblage (i.e. the amount of new biomass it produces per unit time) a power law function of its biomass with a slope of 0.75?…”
    I argue that it’s not. That was an earlier expectation now shown to vary. The Hatton paper cited shows varied power law exponents, as do other papers, such as:
    – Kerkhoff & Enquist. 2006. http://onlinelibrary.wiley.com/doi/10.1111/j.1461-0248.2006.00888.x/abstract
    – Jenkins, DG. 2015. http://onlinelibrary.wiley.com/doi/10.1890/ES14-00409.1/full
    – Jenkins, DG & S Pierce. 2017. http://onlinelibrary.wiley.com/doi/10.1111/1365-2745.12726/full
    The last one above fits alternative models and finds a sigmoidal function is most plausible for a wider range of data than commonly used. That model fits adaptive life history strategy theory (Grime JP & S Pierce. 2012. http://onlinelibrary.wiley.com/book/10.1002/9781118223246).
    All this is to say that metabolic theory expectations (a) set a great agenda for scaling, (b) explain well individual organism scaling, and (c) serve as a “null” that is bent at supra-organismal levels by ecological conditions. I hope that helps aim to a more interesting question, such as “Which factors most strongly shape NPP (etc.) scaling, when and where?” or “How will NPP (etc.) scaling shift with change?”

  6. Pingback: What are the biggest puzzles in ecology? « Nothing in Biology Makes Sense!

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