A while back we invited you to ask us anything. Here’s the next question, from Margaret Kosmala, who clearly knows Brian and I. Question has been paraphrased, click through for the original.
In light of this opinion piece from a physicist, should ecologists be trying to estimate the values of universal (or even conditional) constants, thereby allowing more severe tests of ecological hypotheses?
How did I not know about this until now?!
The above is from the 3rd (2014) Canadian edition of Manuel Molles & James Cahill’s Ecology textbook. “Zombie ideas”! In a textbook!
I’m a bit late to this (sorry, got busy then it slipped my mind), but better late than never. Writing in Nature, Grace et al. 2016 try to slay the zombie idea of a humped diversity-productivity relationship by integrating multiple theories into a single structural equation meta-model that they then fit to data. I don’t ordinarily comment on individual papers from the recent literature. But I’ve been following work on this topic so I thought I’d say a few things. I think there are some important larger lessons here for how to do good ecology.
As regular readers know, I worry a lot about zombie ideas–ideas that should be dead, but aren’t. Zombie ideas are the most important failures of science’s self-correction mechanisms: they’re big, widespread errors or misconceptions that aren’t recognized as such. Over the years, I and our guest posters have identified several zombie ideas in ecology:
The intermediate disturbance hypothesis
Species interactions are stronger and more specialized in the tropics
Humped diversity-productivity relationships
“Neutral” = “dispersal-limited”
Local-regional richness relationships (specifically, the ideas that linear ones are ubiquitous, and that linear ones show that colonization not local species interactions controls local community membership)
And we’re starting to see folks identify other candidate zombie ideas in other venues. For instance, Luke Harmon thinks the notion of ecological limits on continental scale species richness is a zombie idea. I don’t agree, but I can see the argument. Peter Abrams thinks ratio-dependent predation is a zombie idea, though I’d call it a lost cause. Terry McGlynn just listed a couple from his own fields of entomology and tropical biology (three-toed sloths are Cecropia specialists; canopy ants are dominant because of their high-sugar diet).
Here’s my question to you: Is that it? Are those the only zombie ideas in ecology? Or are there others, shambling around unrecognized, eating the brains of the next generation of students even as we speak?* Tell us in the comments: What are the other zombie ideas in ecology?
Remember, zombie ideas are widespread errors. We’re not looking for personal criticisms of individual scientists here, and no such criticism is implied by discussion of zombie ideas. Having proposed or supported a zombie idea doesn’t make anyone a bad scientist. Science is hard and we all get things wrong sometimes.
p.s. I can’t believe I never thought of this post idea before!
*Textbooks are a refuge for zombie ideas.
Statistician Cosma Shalizi is a really sharp guy, who writes wonderfully on everything from technical statistical topics to philosophy of statistics to books about the Soviet Union. The notes for his undergraduate stats courses are online, and they basically comprise a very readable textbook. As part of my prep for teaching intro biostats next term, I was skimming Cosma’s notes, and came across the chapter on linear regression, in which he asks whether R^2 “is a distraction or a nuisance”? Tell us what you really think, Cosma! 🙂
One of the things this blog is known for is calling for the death of zombie ideas–ideas that should be dead, but aren’t. Here, “death” basically means “no longer basing any research on the idea.”
Here are two common ways (among many others) in which some readers have pushed back against those posts:
Both responses highlight the downside risks of abandoning a line of research. And it’s absolutely correct to consider those risks. But of course, just saying “there are downside risks” isn’t enough to determine a course of action, because all courses of action have their own downside risks (and their own upsides). For instance, while we don’t want to throw the baby out with the bathwater, we do want to throw out the bathwater. And while there’s always the risk of giving up on any line of research too soon, there are also risks of giving up too late (e.g., because time, money, and effort spent on a lost cause would be better spent elsewhere).
These are difficult judgement calls to make, and so there will always be disagreement about them.* One way to make these sorts of judgement calls is by drawing on our background knowledge of other similar cases. We’ve talked a lot on this blog about zombie ideas, ideas that should be dead but aren’t. But what about the opposite kind of case? That is:
Has any line of ecological or evolutionary research ever been prematurely abandoned due to criticism from those not pursuing it?
Prematurely abandoned lines of research are the flip side of zombie ideas. They’re dead ideas that should be alive. Ideas that, tragically, left us too soon. I propose calling such ideas Buddy Holly ideas. 🙂 (UPDATE: by “prematurely abandoned”, I mean a line of research that was widely pursued but was abandoned prematurely due to external criticism, analogous to how Buddy Holly became popular but then died in a plane crash. I don’t mean lines of research that were never widely pursued in the first place, even if in retrospect they should’ve been. Such lines of research are more like a singer who never gets discovered.)
Of course, in order to make a strong case that an idea really was prematurely abandoned, it probably needs to be an idea that was later taken up again, successfully. Because unlike Buddy Holly, scientific ideas never perish totally by accident, but always for some reason. So you need to make the case that, even though an idea died for a reason, it wasn’t a good reason.
Note as well that, in order for the subsequent revival of an idea to count as evidence that it’s “death” was premature, the idea needs to be revived in something close to its original form. For instance, while modern research on non-genetic mechanisms of inheritance (maternal effects, DNA methylation, etc.) sometimes is called “Lamarckian”, I think the connections between this modern work and Lamarck’s ideas are far too loose and vague to say that Lamarckianism was prematurely abandoned only to be subsequently revived. Similarly, I think it’s a stretch to call modern evolutionary developmental biology a revival of 19th century German idealist biology (“bauplan” and all that). After all, basically any line of scientific research is going to have some historical antecedent. I mean, there were people who thought that Charles Darwin got his ideas from his grandfather, or from Buffon, or whatever! I’m talking about something much more specific than that.
In an old post I suggested Darwin’s theory of evolution as a possible example of a Buddy Holly idea, since it was “eclipsed” in the late 19th century only to be subsequently revived. Although one can argue about how good an example it is.
Probably the best example of a Buddy Holly idea I can think of is group selection getting abandoned in the late 1960s and ’70s in the wake of criticisms from folks like G. C. Williams and John Maynard Smith, and then revived by folks like David Sloan Wilson. You could interpret the history here as a case of throwing the baby out with the bathwater. Abandoning not only naive, good-of-the-species thinking that really did need to be abandoned, but also viable group selectionist ideas. But I’m not an expert on the history here (which in any case tends to be read differently by different people, I think), so perhaps others can comment.
Perhaps research on food web topology might be an example of a Buddy Holly idea, but I don’t think so. Briefly, back in 1977 Joel Cohen had the creative idea to think of food webs as mathematical objects called graphs (aka networks), with species as “nodes” and predator-prey relationships as “links” connecting predator nodes to prey nodes. Food web data compiled from the literature suggested some surprising general properties of these graphs–for instance, they tended to be “interval”, and the ratio of links to species seemed to be constant (Cohen 1989). And Cohen and others developed simple models to try to explain these apparent patterns. However, the data were of low quality, leading Gary Polis and others to argue powerfully that food web theory was a house built on sand (Polis 1991). But the obvious response to this critique (indeed, the response recommended by Polis himself) was not to abandon this line of research, but to go out and collect better data on who eats whom. Which a lot of people did. Explaining the new patterns in those data subsequently motivated a whole new generation of food web topology models (e.g., Williams and Martinez 2000). So rather than seeing this as a line of research that was prematurely abandoned and then subsequently taken up again, I’d see it as a line of research that only remained productive by taking well-founded criticisms to heart.**
Maybe “randomized null models of species x site matrices as a tool for inferring competition” might be an example of a Buddy Holly idea? Depending on whether you think the revival of interest in that approach since the mid-90s has been productive, or whether you think this approach still is open to some of the same fundamental objections that were raised against it in the late ’70s and early ’80s (I basically take the latter view, but your mileage may vary).
In summary, it looks to me like Buddy Holly ideas are pretty rare, and rarer than zombie ideas. Once a critical mass of researchers decide to pursue an idea, they hardly ever give up on it too soon. Which suggests to me that we don’t really need to worry much that debate and mutual criticism will lead to productive lines of research being abandoned. But what do you think? Are there “Buddy Holly ideas”? Lots of them? Looking forward to your comments.
*If you want to argue that no line of research pursued by professional scientists is ever so unproductive as to merit abandonment, well, ok I guess. But that means you’re ok with not calling for the abandonment of research on ESP, Bigfoot, and tabletop cold fusion, never mind more debatable cases. Or I guess you could say that some lines of research should be abandoned, but that other scientists shouldn’t say so publicly–that it’s best to just publicly ignore lines of research you don’t like. If you can’t say something nice, don’t say anything at all, as the saying goes. Which again, ok I guess. It’s fine if some folks adopt that as their own personal policy. And perhaps in some circumstances it’s the most effective way to encourage abandonment of unproductive lines of research. But personally I’m a little uncomfortable with any argument that says scientists should remain publicly silent about their scientific views, or should never publicly criticize one another’s scientific views. I’m actually not sure if anyone holds such extreme “anti-criticism” views, so I might be addressing a bit of a straw man here. But I’m a believer in thinking through extreme limiting cases, even if they never actually occur in the real world. 🙂
**It probably helped that the criticisms could be addressed in a straightforward fashion. By “straightforward” I don’t mean the criticisms could be addressed easily–collecting diet data for dozens of species in a community is not easy! Rather, I mean it was obvious what sort of new data were needed, and how to obtain them (it was just a lot of work to obtain them). So that addressing the criticisms appeared to many as a really good research opportunity. Criticisms of early observational studies of biodiversity-ecosystem function relationships as confounded by sampling effects were seen in much the same way, I think. People quickly realized how to address the criticisms with new experimental designs and statistical analyses, and so addressing them was seen as a research opportunity. In contrast, when I suggest (as I did at the end of Fox 2012) that the time is ripe for a new generation of work on disturbance-diversity relationships, grounded in modern coexistence theory, it’s not immediately obvious exactly what sort of work that would involve. “Go out and test for storage effects and relative nonlinearity, and see how their strength varies as a function of disturbance frequency and intensity” isn’t straightforward in the way that “go out and assess the diets of every species in a community” is. Or at least, it probably doesn’t seem that way to most people. Put slightly differently, I suspect that calls from Gary Polis and others for better food web data, or calls to address the issue of sampling effects in BD-EF research, sounded to many people like calls to continue the same research programs by different means. While I suspect my call for research on disturbance-diversity relationships to be based on modern coexistence theory rather than the IDH probably sounds to a lot of people like an attempt to change the question, and thus to replace an existing research program with a new (and not clearly-defined) one. Or perhaps I’m wrong, perhaps it’s only with the benefit of hindsight (and perhaps only to my eyes?) that the history of food web research looks like a single continuous research program with a healthy back-and-forth between theory and data? Perhaps at the time, and to those involved, the critiques of Polis and others felt like calls to replace one (in their view failed) research program with an alternative program? I don’t know, just speculating here, comments welcome.
Note from Jeremy: This is a guest post by Angela Moles and Jeff Ollerton. A little while back I noted with interest that Angela had been publishing peer-reviewed papers arguing that some widely-believed generalizations about tropical ecology actually are zombie ideas. Jeff has been doing the same. I found their case convincing, but I’m not an expert on tropical ecology. So I invited Angela and Jeff to write a guest post making their case, in the hopes of sparking a productive debate on what I think is an important issue. Thanks very much to Angela and Jeff for taking the time to write what I think is both a provocative and well-argued piece, drawing on the work of others as well as their own work. Looking forward to a lively discussion in the comments.
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The concept of zombie ideas has been very useful in ecology. It turns out that there are quite a few venerable old ideas out there that should be dead because they have been slain by data and/or theory, but which still wander the world feasting on the brains of ecologists (such as common interpretations of the intermediate disturbance hypothesis; Fox 2013). In this post, we’re going to argue that the idea that species interactions are stronger and more specialized in the tropics is a zombie idea that needs to be slain.
The biotic interactions zombie started life as a perfectly good theory. The idea was that because the weather is always nice in the tropics, populations of plants and animals would not be knocked back by cold winters. The resulting population stability would allow plants and animals to reach high densities. In addition, lower rates of extinction coupled with higher rates of speciation mean that the greater species diversity with tropical communities results in species having to become specialized to exploit narrower niches, e.g. using a single food source. Year-round interactions with high densities of highly specialized attackers would naturally result in more intense (i.e. stronger) biotic interactions in tropical ecosystems, such as higher rates of herbivory and predation (Dobzhansky 1950; MacArthur 1972; Janzen 1973; Pennings & Silliman 2005). Furthermore the arms races resulting from these interactions would lead tropical species to be more heavily defended, and contribute to high diversity in the tropics (Coley & Kursar 2014).
The idea that biotic interactions are more intense and specialized at low latitudes is extremely widely accepted (e.g. Schemske et al. 2009; Coley & Kursar 2014). We both set out to study aspects of this idea with the full expectation that our work would confirm the traditional ideas. However, as the data rolled in, it became clear that many of the links in the lovely chain of logic above turn out to be weak or broken.
First, while the temperature is certainly stable and warm in the lowland tropics, many tropical areas experience substantial seasonality in precipitation (quantified in Vázquez & Stevens 2004). That is, despite all those postcards of sunny tropical islands, the weather isn’t always favourable for growth in the tropics (Figure 1). People who live in the tropics simply call their seasons things like “the dry season” and “the monsoon” rather than “summer” and “winter”, and are more likely to need a nice cold drink than a pair of skis.
Figure 1. A tropical forest during the dry season (Chamela, Mexico). Photo A. Moles.
Empirical data have also not supported the idea that population stability increases toward the tropics. Vázquez and Stevens (2004) compiled data for 12 major groups of mammals, birds and insects. Five taxa showed no relationship between population stability and latitude, 5 actually showed significantly greater stability at higher latitudes, and only 2 showed higher stability at lower latitudes. Meta-analysis showed that the overall effect of latitude on population stability was not significantly different to zero.
The evidence for greater specificity of interactions such as mutualisms, host-parasite and predator-prey relationships in the tropics is mixed, and certainly does not support the idea that the tropics are always more specialized (Ollerton 2012). Where the evidence is clear, such as for biotic pollination and frugivory, interactions are not more specialized in the tropics compared to extra-tropical regions once sampling effort is taken into account, suggesting that assemblages of interacting species in the tropics tend to be under-sampled (Ollerton & Cranmer 2002). More recently, an analysis of mutualistic interaction networks has shown that in the tropics, these networks tend to be LESS specialized (Schleuning et al. 2012). Finally, meta-analysis did not support the idea that species’ niche breadths are narrower at lower latitudes either (Vázquez & Stevens 2004).
Early reviews tended to support the traditional idea that biotic interactions were more intense in the tropics (Coley & Aide 1991; Coley & Barone 1996). However, these findings have been thrown in to doubt by a range of recent syntheses and meta-analyses. The empirical evidence has not supported the idea that terrestrial herbivory (Moles et al. 2011), marine herbivory (Poore et al. 2012), density dependent mortality in plants (Hille Ris Lambers, Clark & Beckage 2002) or seed predation (Moles & Westoby 2003) are stronger at lower latitudes.
In summary, the “strong and specialized biotic interactions in the tropics” hypothesis is dead. The quantitative evidence is counter to its predictions. Further, the chain of logic that led to its prediction of stronger biotic interactions in the tropics (including a stable climate, more stable populations, and more specialised interactions in the tropics) is in tatters. There is certainly scope for more studies on all of these topics, but at this stage it will take something quite substantial to overturn the mass of accumulated evidence against the idea that species interactions are always stronger and more specialized in the tropics. In fact, if there has been publication bias against results contrary to the traditional idea in the past (either through the file-drawer effect (Rosenthal 1979), or from reviewers being harsher on studies they perceived as getting the “wrong” answer), then the publication of syntheses and meta-analyses showing that the traditional ideas are not nearly as strongly supported as we thought (e.g. Vázquez & Stevens 2004; Moles et al. 2011; Ollerton 2012; Poore et al. 2012) might actually lead to a rapid accumulation of evidence contrary to the traditional ideas over the next few years.
Is the biotic interactions idea a zombie? Well, it certainly seems to be getting around a lot for a dead thing. Schemske et al. gave it a very warm review in a 2009 Annual Review of Ecology, Evolution and Systematics paper, and Coley and Kursar (2014) used it to underpin a recent perspective piece in Science.
Studies showing that species interactions are not stronger or more specialized in the tropics do not change the fact that tropical ecosystems are beautiful and amazing places. The observation that some aspects of ecology work in similar ways in tropical and temperate ecosystems is not actually all that surprising, and it means that tropical biologists and ecologists from other parts of the world can work together to advance our understanding of the ways that species interact. Finally, abandoning the idea that biotic interactions are more intense and more specialized in the tropics is like throwing away well-loved but worn out clothes: initially sad, but it will leave room in our collective wardrobe for a whole crop of exciting new ideas. Future progress will require researchers to more clearly define both their hypotheses (perhaps moving from conceptual to formal mathematical models) and their definitions: at least some of the disagreements in the literature stem from different definitions of terms such as “specialized” and “generalized” (Ollerton et al. 2007). This is clear when we consider that tropical communities, on average, certainly contain a higher number of functionally specialized pollination systems (e.g. bee, bird, beetle, fly, cockroach, etc.) and temperate systems have more plants that are functionally generalized (mixed bee/fly/butterfly, etc.) (Ollerton et al. 2006). However tropical plants are not more ecologically specialized, in terms of the number of pollinating animal species servicing each plant (Ollerton & Cranmer 2002). So, depending upon whether we are referring to functional or ecological specialization of plants in tropical communities, we could come to very different conclusions.
It is human to have trouble relinquishing ideas that we liked, and there’s no doubt that the latitudinal biotic interactions hypothesis was a really nice idea that made a lot of intuitive sense. Also, although it’s hard to test, we suspect that television documentaries that have traditionally focussed on highly specialised and intense interactions within the tropics have skewed our vision of what tropical ecology “should” be like, as opposed to what it’s really like, as has the tendency for ecologists to mentally compare tropical rainforests with temperate deciduous forests, ignoring all the other major vegetation types in each region. However, as scientists, we MUST disregard ideas once they have been disproved by data. As Neil DeGrasse Tyson says, “The good thing about science is that it’s true whether or not you believe in it.”
REFERENCES
Coley, P.D. & Aide, T.M. (1991) Comparison of herbivory and plant defenses in temperate and tropical broad-leaved forests. Plant-animal interactions: Evolutionary ecology in tropical and temperate regions (eds P.W. Price, T.M. Lewinsohn, G.W. Fernandes & W.W. Benson), pp. 25-49.Wiley, New York.
Coley, P.D. & Barone, J.A. (1996) Herbivory and plant defenses in tropical forests. Annual Review of Ecology and Systematics, 27, 305-335.
Coley, P.D. & Kursar, T.A. (2014) On Tropical Forests and Their Pests. Science, 343, 35-36.
Dobzhansky, T. (1950) Evolution in the tropics. American Scientist, 38, 209-221.
Fox, J.W. (2013) The intermediate disturbance hypothesis should be abandoned. Trends in Ecology & Evolution, 28, 86-92.
Hille Ris Lambers, J., Clark, J.S. & Beckage, B. (2002) Density-dependent mortality and the latitudinal gradient in species diversity. Nature, 417, 732-735.
Janzen, D. (1973) Comments on host-specificity of tropical herbivores and its relevance to species richness. Taxonomy and ecology (ed. V. Heywood), pp. 201-211.Academic Press, London.
MacArthur, R.H. (1972) Geographical Ecology: Patterns in the Distribution of Species. Princeton University Press, Princeton, New Jersey.
Moles, A.T., Bonser, S.P., Poore, A.G.B., Wallis, I.R. & Foley, W.J. (2011) Assessing the evidence for latitudinal gradients in plant defence and herbivory. Functional Ecology, 25, 380-388.
Moles, A.T. & Westoby, M. (2003) Latitude, seed predation and seed mass. Journal of Biogeography, 30, 105–128.
Ollerton, J. (2012) Biogeography: are tropical species less specialised? Current Biology, 22, R914-R915.
Ollerton, J. & Cranmer, L. (2002) Latitudinal trends in plant-pollinator interactions: Are tropical plants more specialised? Oikos, 98, 340-350.
Ollerton, J. Johnson, S.D.& Hingston, A.B. (2006) Geographical variation in diversity and specificity of pollination systems. Plant-Pollinator Interactions: from Specialization to Generalization (Eds N.M. Waser & J. Ollerton), pp. 283—308. University of Chicago Press, Chicago,USA.
Ollerton, J., Killick, A., Lamborn, E., Watts, S. & Whiston, M. (2007) Multiple meanings and modes: on the many ways to be a generalist flower. Taxon, 56, 717-728.
Pennings, S.C. & Silliman, B.R. (2005) Linking biogeography and community ecology: Latitudinal variation in plant-herbivore interaction strength. Ecology, 86, 2310-2319.
Poore, A.G.B., Campbell, A.H., Coleman, R.A., Edgar, G.J., Jormalainen, V., Reynolds, P.L., Sotka, E.E., Stachowicz, J.J., Taylor, R.B., Vanderklift, M.A. & Duffy, J.E. (2012) Global patterns in the impact of marine herbivores on benthic primary producers. Ecology Letters, 15, 912–922.
Rosenthal, R. (1979) The “File Drawer Problem” and tolerance for null results. Psychological Bulletin, 86, 638-641.
Schemske, D.W., Mittelbach, G.G., Cornell, H.V., Sobel, J.M. & Roy, K. (2009) Is there a latitudinal gradient in the importance of biotic interactions? Annual Review of Ecology, Evolution and Systematics, 40, 245-269.
Schleuning, M., Fründ, J., Klein, A.-M., Abrahamczyk, S., Alarcón, R., Albrecht, M., Andersson, G.K., Bazarian, S., Böhning-Gaese, K., Bommarco, R. et al. (2012) Specialization of mutualistic interaction networks decreases toward tropical latitudes. Current Biology, 22, 1925-1931.
Vázquez, D.P. & Stevens, R.D. (2004) The latitudinal gradient in niche breadth: concepts and evidence. American Naturalist, 164, E1-E19.
Dynamic Ecology 