What ecological questions or topics require no further research?

Recently ran across an interesting remark from Dan Davies: the question “Does the MMR vaccine cause autism?” is one of the few on which scientists have concluded that no further research is needed.

Which got me thinking: what ecological questions or topics require no further research?

There are many boringly obvious answers. For instance, we don’t need any further research to know if species richness tends to be higher in the tropics, or tends to increase with area. Ok, maybe we need more research into why those patterns are observed, or the precise quantitative shape of the richness-latitude or richness-area relationship, or etc. But we don’t need any more research merely documenting the existence of those qualitative patterns. They’re already well-established facts. “Is anthropogenic climate change occurring?” is another boringly obvious answer. There are many topics related to climate change that require further research. But the basic fact that the climate is changing because of human activities doesn’t need any further research to establish it.

So what are the less obvious answers? What ecological question has only recently been answered so definitively that further research isn’t needed? You tell me! The more interesting/important the question, and the more recently it’s been definitively answered, the better. You get bonus points for boldness if you can make a good argument for cessation of research on a question that’s still actively being researched. (As opposed to a question on which active research has already ceased because everyone agrees that the question has been definitively answered.)

The first (slightly) less obvious answer that occurs to me is “the shape of the biodiversity-ecosystem function relationship”, in experiments manipulating species diversity within a single trophic level, in which the function of interest is the total productivity or biomass of those species. But that’s still a fairly boring answer; I think most ecologists would agree that issue was resolved years ago. But other people have more interesting answers. Over at Ideas For Sustainability, Joern Fischer suggests that there’s nothing really new to learn about conservation and sustainability. He argues that what’s needed is action, not adding unimportant nuances to existing knowledge. And here’s a related old post in which I asked “What ecological controversies are now settled?”

It’s perhaps worth noting that the question “Does the MMR vaccine cause autism?” is one that few scientists thought needed any research in the first place, as far as I know. Which if so would explain why nobody now thinks any further research is needed. Off the top of my head, I can’t think of any similar cases in ecology. Though I bet there are some that I’m just not aware of.

A final thought: are there ecological questions that don’t require further research because we already have a definitive answer, and that definitive answer is “it depends” or “it’s complicated” or “it varies idiosyncratically”? In an old post, I argued that we don’t need any more research on whether the local-regional richness relationship is linear or saturating, because we now know the answer is “it varies idiosyncratically” and because there’s good theoretical reason to expect idiosyncrasy.

Note that I’m not looking for cases in which no further research is needed because the question is ill-posed or unanswerable. Nor am I looking for cases in which no further research is needed because nobody cares about the question any more, even though it has yet to be answered.

Looking forward to your comments, as always.

 

21 thoughts on “What ecological questions or topics require no further research?

  1. Another difference between the question “Does the MMR vaccine cause autism?” and most ecological questions is that answering the former doesn’t suggest any further questions. At least not if the answer to the former is “no”.

    Well, that’s how it seems to me as someone who’s not a vaccine researcher, anyway. But perhaps I’m wrong about that?

  2. I’m not convinced that “further research to know if species richness tends to be higher in the tropics” is equivalent to “does the MMR vaccine cause autism?” in the terms that you are setting out Jeremy. Hillebrand’s 2004 study (and the more recent follow up) of the generality of the latitudinal gradient certainly indicated that there’s a general pattern, but it’s far from being a rule in the sense that “MMR vaccine does not cause autism”. There are significant groups of organisms which do not peak in their richness in the tropics but which have hardly been studied in this regard. Bees are a good example, where species richness seems to peak in dry, warm-temperate habitats, not the tropics. However this has not been assessed seriously – I have published a couple of graphs on the topic based on comments in Michener’s book, but that’s about it. Most taxa have hardly been looked at in this regard.

    There’s also the question of whether “latitude” per se is really an ecological factor, and that primary productivity or climatic stability of an area are really the factors that should be assessed. Once you start to bring that into play, the relationship between species richness and latitude begins to look much more complex, especially if you consider patterns in the global south.

  3. A lot of your examples come down to pattern vs process. We have some highly repeatable patterns in ecology like species abundance distributions and species are relationships and latitudinal gradient at say the class level and up, and also some highly variable patterns like local vs regional richness or productivity-richness or even latitudinal gradient at say family or genus level. I’m not sure we need more research on these patterns. And to the extent we are going to divert research to patterns we should focus on some other areas (e.g. body mass distribution local regional relationships).

    In some cases like the SAD I’m not sure we really need more work on processes. But most of these areas we still have a lot to learn about processes.

    So it just depends on what grain size of question you consider to be interesting to consider as final.

    Its also interesting to note how much better ecology is at pattern than process.

    • “Its also interesting to note how much better ecology is at pattern than process.”

      Now I’m wondering, what are the best-established process-related claims in ecology? Not case studies–we have plenty of great case studies that establish processes. But process-based claims that apply at least in an approximate way to many different cases/systems/species/whatever.

      Lake eutrophication would be a big one, I think.

      Predator and competitor removal experiments give pretty consistent results in different systems, at least at a qualitative level. For instance, if you remove predators, you basically always get a trophic cascade, the strength of which attenuates at the plant level as compared to the herbivore level (Shurin et al. 2002). Does that count as a well-established generalization about process?

      How about “population growth generally is density-dependent, although the strength often is too weak to distinguish from zero given the typical length of ecological time series and typical sampling error”? (Ziebarth et al. 2010)

      (Aside: I’m actually totally fine with having lots of good case studies of this or that processes but few meta-analytical generalizations about process. But I know others would find that a dissatisfying state of affairs…)

      • You’re right. Ecologists are also good at processes (both theory and empirical tests). But tying the two together is what we’re not good at.

        I, for one, wouldn’t necessarily agree we have great patterns from predator or competitor addition/removal experiments other than fairly trivial of the obvious effect at the most immediately adjacent species (i.e. direct interactions) in the obvious direction. But that is almost tautological – the definition of competition is it spress the per capita growth rate of species and similarly for predation. I agree trophic cascades would be less trivial but I don’t see them as quite as strongly established, especially in food webs as opposed to food chains. Similar with eutrophication – adding a limiting resource increases carrying capacity.

        But going deeper we’ve never taken the generalized Lotka-Volterra theory to any sort of general pattern.

        I suppose as a pattern-first macroecologist I have a strong standard for what counts as an interesting pattern. Goes back to my evils of ANOVA post. I’ve never found X affects Y (even if general or even if the direction of effect is a priori) very satisfying.

        Although “trivial” or “tautological” is obviously in the eye of the beholder, I’m tempted to suggest we’ve never linked pattern and process at a level beyond the trivial or tautological.

        There’s almost like a Heisenberg uncertainty principle. You can know the pattern or you can know the process, but you cannot know both.

      • “You can know the pattern or you can know the process, but you cannot know both.”

        Perhaps because many of the most ubiquitous patterns are ubiquitous because they’re statistical attractors (https://dynamicecology.wordpress.com/2014/06/30/steven-frank-on-how-to-explain-biological-patterns/). They’re ubiquitous because almost any ol’ process would give rise to them, and few if any wouldn’t.

        I think that’s part of what makes the latitudinal species richness gradient tantalizing–it’s hard to see how it could be a statistical attractor.

      • No disagreement from me about statistical attractors. I think you & I are 2 of about 5 ecologists in the world who find that a satisfying explanation.

        While I agree that statistical arguments are hard to imagine for the latitudinal gradient (aside from the spatial structure mid-domain argument which I think has some real problems). yet it is amazing how many systems show this pattern including human languages and human cultures and I think lists of recipe ingredients and etc. I am not aware of a single system where the number of “types” increases to the pole (and only highly non-biological systems like minerals where it is flat vs latitude). This finding the pattern in diverse (non-ecological) systems is a hallmark of statistical attractors (SAD of hard disk file sizes, make/model of cars in a garage, etc). Whatever the explanation for the latitudinal gradient. it cannot be highly ecologically specific although it might be biologically specific.

      • “I think you & I are 2 of about 5 ecologists in the world who find that a satisfying explanation.”

        Ok, I’m going to do some polls on this. Ask readers what senses of “generality” they care about. And also ask which patterns in ecology they think are statistical attractors.

        “aside from the spatial structure mid-domain argument which I think has some real problems”

        Don’t get me started. The mid-domain effect is SO not a thing.

        “lists of recipe ingredients”

        Wait, what? I can see how that might be true as a side effect of the latitudinal gradients in plant and animal species richness, plus the inability of many crops to grow at very high latitudes. But still, I want to see a link for that!

        Yes, you’re right that “we see the same pattern in car models/frying pan sizes/whatever as we do in species” is often a sign that you’re dealing with a statistical attractor. But I’m reluctant to take it as diagnostic; I want to see the statistical attractor argument spelled out.

      • Jeff – sure – some of those are classic. That’s why I stated my claim carefully as being at the class level or above (e.g. birds, molluscs). It is hardly shocking that if you go to the family or genus level where there are often hundreds you will find some counterexamples. And I suppose I was slightly too strong in my claim of not knowing any categories increasing to the poles (I was thinking about non-species-richness examples when I wrote it).

        The aphids are sub-class (sub-order I think?) but still a large group but they used ratio of aphid species to plant species which is hardly the same thing.

        NA breeding birds is a wonderful example that is strongly suggestive of mechanism – their wintering distribution follows the latitudinal gradient and the summer distribution follows very closely the summer productivity IF you home in just on continental North America north of Mexico and south of Northern Canada (i.e the area classicaly covered by the NA breeding bird survey but a pretty spatially cherry-picking region). If you take the whole continent you still have a latitudinal gradient that has a strong trend to most species at the equator. I’m a coauthor on a paper by Lars Dalby that homes in on ducks and very strongly fingers productivity variables rather than others (like day length).

        I think marine macroalgae may be similar.. In general the new Tittensor and Worm book does a nice job of pulling out marine examples which are not always simple pole-equator (e.g often benthic-pelagic) which are elucidative of mechanism.

        But I’m not sure there is an example of a class or kingdom for a whole hemisphere that is an exception?

      • OK Jeff – I know I’m bound to lose this argument because I’m trying to claim there is a general rule in ecology and all you have to do is produce one counter-example to win. So I stipulate you win. But I’m not going down easy either!

        So gymnosperms:
        a) their richness peak is subtropical – its not temperate-boreal like a lot of people would think, it’s not inconceivable that the same general processes are driving them with a special case causing the depression in richness in the tropics, towards which point …
        b) Yes you are right gymnosperms are be a phylum and each subgroup a class to destroy my class claim. But they’re really small classes and even a tiny phylum (1500 species?). And how many ecologists go out and sample only gymnosperms. Not many because they’re not really an ecologically isolated guild. They are clearly competing with angiosperm trees (or trees and shrubs) and so like many other smaller taxa that appear to be counterexamples they are on some level just getting squeezed poleward by some other closely related taxa of a larger group of which they are part. Its just that gymnosperms are a “class” because they are an old and relictual group. Which makes me wonder what the latitudinal gradient in sharks and horse-shoe crabs?

        So my new claim: latitudinal gradients exist in taxonomic groups or ecological guilds sensu latu with at least 5000 species when considered a hemisphere at a time.

        I eagerly look forward to your counterexamples to this!

      • Ha ha, you’re a gentleman and a scholar Brian ๐Ÿ™‚

        OK, point taken re gymnosperms, though again conifers buck some of what you say. They are ecologically dominant in some areas of course, including temperate and subtropical mountains where one would have thought that angiosperms would have the upper hand. And I believe I’m correct in saying that there is evidence that extant taxa have radiated recently, even though the group as a whole is more ancient. But I agree, the pattern is an oddity.

        Putting “class” into quotes reminded me of something that I wanted to add, which was that, as I’m sure you recognise, taxonomic groups are to a large extent arbitrary divisions that we impose. But if we’re looking for a large (~20,000 species), ecologically important clade that bucks the trend, then (as I mentioned above) the bees are the best example. Species richness seems to peak in dry, warm-temperate habitats, not the tropics or even the subtropics – see Figure 2 in my AREES review:

        https://jeffollerton.wordpress.com/2017/11/11/pollinator-biodiversity-and-why-its-important-a-new-review-just-published-download-it-for-free/

        But, again to repeat, this graph is about as seriously as the pattern has been assessed โ€“ and this is a very well researched group of insects. What patterns are out there for less well researched groups? The Ichneumonidae, with at least 25,000 species, were thought to be another example but that’s been challenged and the jury is out. Suggesting that there is still work to be done for some large clades in understanding their latitudinal distribution:

        https://en.wikipedia.org/wiki/Ichneumonidae#Distribution

      • OK – Jeff – here is where I have to acknowledge you win. Any arguments against bees as a taxonomically rich, ecologically real and mostly taxonomically valid group is sophistry.

        It is interesting how poorly known some really major groups still are. I was shocked how poorly we’ve pinned down even the number of gymnosperms.

      • It’s not the winning, Brian, it’s the taking part ๐Ÿ™‚ Yes, I have to agree, there are incredible gaps in our knowledge, even things that we “know” that we know are often built on the flimsiest of evidence. It’s why I’d never stop challenging patterns or pushing for more data to test patterns, even before we get to the processes. This is one of the values of DE and the other ecology blogs, it allows to us to discuss these things in real time. Steve Heard has just posted a terrific example if you’ve not seen it: https://scientistseessquirrel.wordpress.com/2019/06/25/its-been-a-while-since-ive-been-this-proud-of-a-paper/

      • Indeed! These kinds of conversations are why I value blogging. Our conversation has definitely pushed & advanced my thinking. The only other way I get these kinds of conversations is conferences & working groups which have a much higher carbon footprint.

  4. That’s a very important reflection. Nevertheless, it’s complicated to consider any scientific problem as solved in ecology or any other discipline. How many times have physics or chemistry been falsely dubbed finished? History shows that any scientific cold case might be reheated by a novel perspective, a synthesis, or an integrative theory. I agree with Brian that in many cases what we lack in ecology is the investigation of processes in addition to patterns. Or some creative theoretical synthesis. Many ecological theories and frameworks may be considered valid but weak from a Lackatosian view, as they have a hard time consolidating their hard core. So there is much work to be done even in fields with huge literatures.

  5. The world is changing. We don’t need more research on “is biodiversity higher in the topics?” But we might need to check in 100 years or so that’s still the case.

  6. ‘Are communities structured by top-down or bottom-up processes?’ was the sort of question posed at one time. I am not sure the question would be posed in the same way now. It is either answered with ‘it depends’ or ‘both processes are involved’, or perhaps could be argued that it is a poorly posed question.

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