Although the notion “bandwagon” technically only means something that is rapidly growing in popularity, calling a scientific research program a bandwagon carries several more connotations. These include the idea that it will crash (people will abandon it) and that people are piling in because they perceive the research program as a way to do something that is “easy” (or even formulaic) but still get in a good journal (i.e. the proverbial something for nothing). Popular and easy are of course two of the worst reasons to choose a research project, but that seems not to matter in the bandwagon phenomenon.
There is little doubt that functional traits are a bandwagon research program right now:
The use of the phrase “functional trait*” (per Web of Science) is rising exponentially with a doubling time of less than 4 years. In less than two decades, there are almost 3000 total publications cited 56000 times, 14000 times last year alone (with an astonishing average citation rate of 19 times/article and an h-index for the field of over 100).
For better and worse, I am probably one of a fairly large group of people responsible for this bandwagon due to this paper which came out simultaneously with a couple of other papers arguing for a trait based approach, although (as likely true of all bandwagons) the idea has been around much longer and builds on the research of many people.
By calling functional trait research a bandwagon, I am implying (and now making explicit) two things: 1) The popularity of the functional trait program is in part due to the fact that people see it as a simple way to do something trendy. I think there is no doubt of this – there are a lot of papers being published right now that just measure a bunch of functional traits on a community or guild and don’t do much more. 2) That this party is about to come to an end. I predict we will see multiple papers in the next two years talking about how functional trait research is problematic and has not delivered on its promise and many people bailing out on the program.
You might think I am worried about the impending crash, but I am not. I actually relish it. Its after the bandwagon crashes that we lose all the people just looking for a quick paper and the people who are really serious about the research field stay, take the lessons learned (and identify what they are), build a less simple, more complex but more realistic, productive world view. In my own career I have seen this with phylogenetic systematics, neutral theory of biodiversity, and – if we go back to my undergraduate days – neutral theory of genetics and island biogeography.
In an attempt to shorten the painful period and hasten the renewal, what follows are my ideas/opinions about what is being ignored right now on the functional trait bandwagon (although by no means ignored by the researchers I expect will still hang around after the crash and I have tried to give citations where possible), which I predict will become part of the new, more complex view of functional traits version 2.0 in 5-10 years down the road.
(As an aside – I wanted to briefly note as a meta comment on how I think science proceeds, that: a) I think probably many other people are thinking these thoughts right now – they’re in the air, but as far as I know nobody has put them down as a group in ink (or electrons) yet and b) my own thinking on this has been deeply influenced by at least a dozen people and especially by Julie Messier as well as Brian Enquist & Marty Lechowicz – more full acknowledgements are at the bottom c) its not as easy to assign authorship on these thought pieces as it is on a concrete piece of experiment or analysis – if this were a paper I could easily argue for just myself as author or 1 more or 3 more or 10 more)
So without further ado, here are 9 things I think we need to change to steer the bandwagon:
- What is a trait? – there are a lot of definitions (both the papers linked to above have them). But the two key aspects are: 1) measured from a single individual and 2) conceivably linked to function or performance (e.g fitness or a component such as growth rate). The 2nd is not a high bar to clear. But a lot of people right now are ignoring #1 by taking values that can only be tied to a species or population (such as population growth rate, geographic range size, mortality rates) and calling them functional traits. They’re not. They’re important and interesting and maybe science will someday decide they’re more important than things you can measure on individuals. But they’re not functional traits if you can’t measure it on one individual. The functional trait program is going from function (behavior and physiology) to communities or ecosystem properties. Its where a lot of the excitement and power of the idea comes from. It is actually in a subtle way a rejection of the population approach that dominated ecology for decades.
- Where’s the variance? – I believe that the first step in any domain of science is to know at what scales and levels of measurement variation occurs. Only then can you know what needs to be explained. There has been an implicit assumption for a long time that most of the variance in functional traits is between species and/or along environmental gradients. There is indeed variation at these two levels. But there is also an enormous amount of variation between individuals in the same species (even population). And there is way more variation between members of a community than between communities along a gradient. Finally, although the previous statements are reasonably general, the exact structure of this variance partitioning depends heavily on the trait measured. Functional traits won’t deliver as a field until we all get our head around these last three facts. And learn a lot more than we already know about where the variance is. A good intro to this topic is Messier et al 2010 and Viollet et al 2012 (warning I’m a coauthor on both).
- Traits are hierarchical (can be placed on scale from low level to high level) – we tend to lump all traits together, but traits are hierarchical. Some are very low level (e.g. chlorophyl concentration per leaf volume), one level up (e.g. light absorption), and going on up the ladder from this one trait we have Amax (maximum photosynthetic rate), leaf CO2 fixation/time, CUE (or carbon use efficiency or assimilation over assimilation+respiration), plant growth rate, and fitness. Note that each trait directly depends on the trait listed before it, but also on many other traits not listed in this sequence. Thus traits are really organized in an inverted tree and traits can be identified at any tip or node and performance sits at the top of the tree. We move from very physiological to very fitness oriented as we move up the tree. One level is not more important than the other but the idea of different levels and being closer to physiology or closer to fitness/performance is very real and needs to be accounted for. And we need to pick the right level for the question. All traits are not equivalent in how we should think about them! And learning how to link these levels together is vital. A depressing fact in phenotypic evolution is that the higher up the hierarchy a phenotypic character is, the less heritable it is (with fitness being barely heritable), but so far we seem to be having the opposite luck with functional traits – higher level traits covary more with environment than low level traits (there are a lot of good reasons for this). A good intro paper to this topic is Marks 2007.
- Traits aren’t univariate and they’re not just reflections of 1-D trade-offs – How many papers have you seen where trait #1 is correlated with environment. Then trait #2 is correlated with environment, and etc.? This is WRONG! Traits are part of a complex set of interactions. If you’re a geneticist you call this epistasis and pleiotropy. If you’re a physiologist you call this allocation decisions (of resources). If you are a phenotypic evolution person you call this the phenotypic covariance matrix. Of course we are finding that one trait low in the hierarchy is neither predictive of overall performance nor strongly correlated with environment. It is part of an intricate web – you have to know more about the web. The main response to this has been to identify trade-off axes. The most famous is the leaf economic spectrum (LES) which basically an r-K like trade-off between leaf life span and rate of photosynthesis. Any number of traits are correlated with this trade-off (e.g. high nitrogen concentrations are correlated with the fast photosynthesis, short life end). And several of the smartest thinkers in traits (e.g. Westoby and Laughlin) have suggested that we will find a handful of clear trade-off axes. I hate to contradict these bright people, but I am increasingly thinking that even the idea of multiple trade-off axes is flawed. First the correlations of traits with the LES are surprisingly weak (typically 0.2-0.4). Second, I increasingly suspect the LES is not general across all scales. And the search for other spectra have gone poorly. For example, despite efforts, there has not yet emerged a clear wood economic spectrum that I can understand and explain. So to truly deal with traits we need to throw away univariate and even trade-off axes and start dealing with the full complexity of covariance matrices. This is complex and unfortunate, but it has profound implications. Even the question of maintenance of variation simplifies when we adopt this full-blown multivariate view of phenotype (two nice papers by Walsh and Blows and Blows and Walsh). For a good review of the issue in traits see the newly out just this week in TREE Laughlin & Messier
- Any hope to predict the performance consequences of traits requires dealing with the TxE (traitXenvironment) interaction – Does high SLA (specific leaf area or basically thinness of leaf, a trait strongly correlated with the rapid photosynthesis end of the LES) lead to high or low performance? The answer blatantly depends on the environment (e.g. causes lower performance in dry environments or environments with lots of herbivory). Too many studies just look at trait-performance correlations when they really need to look at this in a 3-way fashion with performance as a 3-d surface over the 2-D space of trait and environment. Presumably this surface will usually be peaked and non-linear as well (again see Laughlin & Messier 2015)
- Theory – the field of functional traits is astonishingly lacking in motivating theory. When people tell me that natural history or descriptive science is dead, I tell people its just been renamed to functional traits. I personally see descriptive science as essential, but I also see theory and the interaction between theory and description as essential. Key areas we need to develop theory include:
- How exactly filtering on traits works – one of the appealing concepts of traits is that we can move from simply saying a community is a filtered set of the species pool to talking about what is being filtered on. But we aren’t thinking much about the theory of filtering. Papers by Shipley et al 2006 and Laughlin et al 2012 are good starts but not referenced by most workers in the field. And nowhere have we got a theory that balances the environmental filter that decreases variance with the biotic competition filter that increases variance within a community (and yes Jeremy, other possibilities are certainly theoretically possible per Mayfield & Levine 2010, but for good empirical reasons, I believe this is the main phenomenon happening in traits).
- What is the multivariate structure of trait covariance – This is partly an empirical question but there are many opportunities for theory to inform on this too. In part by thinking about …
- Causes of variation – we know variation in traits are due to a combination of genetic variation and adaptive plasticity and that these respond to environments at many scales. But can we say something quantitative?
- Individuals – we are very caught up in using traits as proxies for species but I increasingly think that filtering happens on the individual level and that we need to shift away from thinking about traits at the species level. The same given trait value (say the optimal value in some environment) can be provided by any of several species, each species of which shows consider variability in traits and therefore having significant overlap in the trait distributions between species.This idea can be found in Clark 2010 and Messier et al 2010 among many others. This might seem subtle, but it is a pretty radical idea to move away from populations to individuals to understand community structure.
- Interaction traits, reproduction traits and other kinds of traits – most of the traits studied are physiological/structural in nature. This is probably because one of the major roots of functional traits has been seeking to predict the ecosystem function of plants (e.g. CO2 fixation, water flux). But if we are going to develop a fully trait-based theory of ecology we need to address all aspects of an organism including traits related to species interactions (e.g. root depth for competition, chemical defenses for herbivory, floral traits for pollination and reproduction, and even behavioral traits like risk aversion).
- Traits beyond plants – the trait literature is dominated by botanists. There is a ton of work in the animal world that deals with morphology and behavior. And some of it is starting to be called “functional traits.” The hegemony of one term is not important, but the animal and plant people thinking about these things (whatever they’re called) need to spend more time communicating and learning from each other.
So there you have it. If you want to predict outcomes (e.g. invasion, abundance, being found at location X or in environment Y, and etc) based on traits, its easy. You just have to recognize that it happens in interaction with the environment and many other traits (many of which we haven’t even started studying) and figure out what the appropriate level of traits to study for the scale of the question. Sounds easy right? No, of course not. When is good science ever easy? That’s the problem with bandwagons. Anybody want off the trait bandwagon before we get to that destination? Anybody want on if they know that is the destination?
What do you think? Are traits a bandwagon? Is it about to crash? What will be the story uncovered by those picking up the pieces? Anything I forgot? Anything I should have omitted?
PS – I don’t usually do acknowledgements on informal blog posts, but it is necessary for this one. My thinking on traits has been profoundly influenced by many people. First among them would be Julie Messier who is technically my student but I am sure I have learned more from her than vice versa. And she currently has shared with me several draft ms that make important progress on #2, #4 and #5. I also have to highlight my frequent collaborators, Marty Lechowicz and Brian Enquist. Also influencing me greatly at key points are Cyrille Violle, Marc Westoby, Evan Weiher. And this field is advancing by the work of many other great researchers (some of whom I’ve mentioned above) who were there before the bandwagon started (and many before I got on) and will still be there after it crashes but whom I won’t try to name for fear of leaving somebody out. Despite it being a bandwagon right now, there is no lack of smart people trying hard to steer constructively!
Hi Brian, nice post! One comment:
The problem with pulling publication trends from Web of Science (like in your figure) is that the production of all ecological papers has grown considerably, and so your figure may, to some degree, just reflect that. I wonder how the figure would look like if you control for that. But at the same time I know that it is a pain, because WoS won’t let you make a report if your search term is too general (e.g. “ecology”); but maybe there is some elegant way around that.
You are of course right – all papers in science and all papers in ecology are growing exponentially as well. Somebody suggested in a DE comment a while back an easy way to correct for this but I am having trouble finding it. A recent estimate (http://blogs.nature.com/news/2014/05/global-scientific-output-doubles-every-nine-years.html) is that publications doubles every 9 years. My graph shows that the doubling time for functional trait papers is less than four years. Simplistically that means the share of papers devoted to functional traits of all literature is more than doubling every
In the end though, I don’t think many people would argue that traits is a giant growing movement in ecology.
To me the more impressive facts are the absolute numbers – 600 publications last year and an h-index of 100.
You’re thinking of this comment of Chris Klausmeier’s:
Chris’ rough data imply a doubling time of about 9-10 years for the ecological literature as a whole.
I’ll just leave this here: http://oregontomb.com/1Kr3d3b 🙂
I wouldn’t write an obituary just yet! Very few bandwagons this big die – they just become more complex and the people not scared away start figuring out the complexities slowly.
Your last point was interesting to me, because in reading the post up until that point, I was thinking, “Huh, I guess I’m working on functional traits?” I never describe it that way, but we measure things like foraging rate and then try to understand how they influence community-level interactions, like those between host and parasite.
Although I could give a nuanced differentiation, functional traits has a lot to do with just “phenotype” and a lot of people are studying phenotypes of course. I do think the functional trait approach has some advantages (amongst others it branches across morphology, physiology, behavior and treats them as a unified concept). But if more functional trait people read literature in the animal world we would be better off.
Not in the animal kingdom but at least in ponds, Elena Litchman and Chris Klausmeier are doing really nice work on functional traits and phytoplankton bridging much of the well developed approach to phenotypes there with the functional trait literature.
A *very* belated comment. I just came back to this post as background reading for a post I’m planning to write about functional trait ecology. I was planning to write about the Litchman-Klausmeier work as some of the best “trait-based” work I know of. But then I read your first bullet point about how if it’s not a number that can be measured on an individual organism it’s not a “trait”. So I went “Huh, so Litchman-Klausmeier doesn’t count?” Because of course their “trait” data are measurements on the performance of *populations* of unicellular algae in chemostats (though some of the “traits”, like cellular nutrient quotas, are parameters that in principle could be measured on single cells). Further, insofar as trait-based ecology is supposed to be a subtle repudiation of population ecology, Litchman-Klausmeier is not trait-based ecology, because it is *very* population ecological. The “traits” are parameters in the Droop model! (which for any readers who don’t know is a standard mechanistic population ecology model for phytoplankton) Litchman-Klausmeier also considers only species-level traits, not intraspecific variation.
But then I read the comments and saw that, actually, you consider Litchman-Klausmeier a fine example of functional trait work after all! And your post does highlight some reasons why. It’s well-grounded in theory (population ecological theory, though). It involves traits related to species interactions in a well-understood way. It identifies higher-dimensional trade-offs among traits rather than 1-D trade-offs.
I guess my point is that some of your desiderata for functional trait ecology are in tension with one another. In particular, I question whether you can have a functional trait ecology that on the one hand is well-grounded in theory and really susses out how “environmental filtering” works, but on the other hand somehow repudiates or downplays population ecology. I think Litchman-Klausmeier highlights those tensions.
Ok, I think I just wrote a rough draft of my post… 🙂
I have always had difficulty understanding how it is that functional trait ecology is different from everyday ecology, and Meghan’s comment summarizes my thoughts quite well.
I have my fair share of issues with functional trait ecology, but the main one is your point #6. What are the expectations for functional traits based on what we know about species interactions, environments, and physiology? I see in your post and in a comment below that environmental filters remove trait variation and competitive interactions increase it. Where do these ideas come from?
In nature, it may be extremely difficult to ameliorate the environmental and competitive effects to see whether such variance modifying processes actually fit. It’s unclear to me how functional trait ecology isn’t just rediscovering the wheel.
But as always, your posts provide great food for thought! Thanks!
You’re absolutely right to highlight #6 as particularly important. People’s intuitive expectations as to how “functional traits” should affect (or even relate to) other variables of interest often are completely rubbish. A small example illustrating my point (warning:shameless self-promotion ahead):
And the blog post that lead to that paper:
And the blog post summarizing the paper:
I certainly agree we need more and better theory on this. All I’ve is express my intuition. To be honest I’m not sure this is subject to experimental manipulation. Which makes theory all the more important. I can give you a handwavy theory of why I expect what I expect. But we need more work for sure.
Decomposing the variation is absolutely key. We recently found that 72% of the variation in thermal maxima in ants that has been documented from around the world can be found in one Panama rainforest (the value is 50% for some well studied temperate fauna). That means comparisons of “tropical” vs “temperate” species and their responses to changing climate are likely missing a huge source of resilience. And that’s before we know how this phenotypic variation arises.
Moreover, when you look for tradeoffs among thermal traits in this assemblage, they aren’t there. It as if these species are being constructed from a menu: one value from Trait A, one value from Trait B… Part of this is lack of tradeoff likely results because we are looking for tradeoffs in traits that are a few steps removed from survival and reproduction (“thermal maxima vs top speed” is not the same as “egg size vs egg number”).
But the other thing that Brian points out, and is absolutely dead-on, is that these populations are also interacting. As a result, there is likely opportunity in that far corner of niche space, if only you can build a phenotype that can get there. Its hard not to think that the trait distribution of communities is not only conforming to environmental gradients, but, that population interactions within that community serve to weaken that trait-environment correlation over time, and in turn make higher-level features of communities: overall abundance, diversity, productivity, more stable.
If so, maybe we should look for the strongest signal in trait-environment correlations (=”filtering”?) in the most disturbed, open communities?
Really interesting examples. I think that your ratios of 50-70% of all variation on earth occurring within a single community is pretty typical. And it really changes the way we think about things. Although you can invoke heterogeneity within your site, its hard to make it credible that it is greater than the variation between temperate and tropics. At that point you have to go looking for some other explanation for the incredible variation within a site. Although there are multiple possibilities (e.g. drift), it is really hard to not start looking hard at species interactions.
Interesting hypothesis at the end!
And just to comment on myself, I think the statement 50-70% of all variation found on earth can be found in a single community is a way more powerful statement than saying x% of all species on earth in some taxon can be found in one community. What does the latter even mean? Is x% a lot or a little. Can it even begin to point to mechanisms beyond sampling type mechanisms? This is one of the reasons I think functional traits is an important approach to community ecology
Fantastic post Brian – absolutely agree.
I review WAY too many papers that correlate a functional trait with some other trait/environmental variable with near zero theory/proposed mechanism/reason for interest in the answer. These aren’t getting us anywhere.
I liked your point about individuals. Functional trait ecology really needs to address the fact that most of our theory quietly pretends that species are the level at which selection happens.
Hi Angela – I expect being asked to review the flood of trait papers even more than I am, and doing lots of thoughtful trait work yourself, you probably have your own version of this list. Would love to see it some time!
It would be good for my thinking to do that…but not right now!
Hi Brian et al. nice stuff. Certainly some interesting observations and ideas. My own personal favourite bandwagon is community phylogenetics: even easier to gather the data, even less theory. (Howls of disagreement expected.)
True, theory is often lacking in some traits papers, and I agree entirely that just expecting traits to solve one’s (vague) problems is unrealistic.
But I still think that trait research that is targeted at generalisation is useful. If we want to achieve some useful knowledge about a species (or species set) about which we currently know little, then how do we do it? To me the Wallacean shortfall (how little we know about the ecology of most species) is the major motivation for working with traits. cheers. Peter
“My own personal favourite bandwagon is community phylogenetics: even easier to gather the data, even less theory. (Howls of disagreement expected.)”
Did you mean howls of agreement? 🙂
Bandwagons have lots of momentum, by definition. But a lot of smart people got off that bandwagon years ago (or started pushing back against it). The writing’s on the wall, even though I think it will take a while for lots of people to realize it.
I agree with your point about Wallacean shortfall as a major reason to do traits. And I hope I was clear. I did not argue to stop doing traits, just to do traits better.
Hi Brian – there is a lot of great content in this post to help out young scientists like myself, who are relatively new to thinking about functional traits. But I have a few comments on the “bandwagon” part of it. First, do you think the “bandwagon” is perpetuated in part by the riders? For example, I’m working in a system where some of the most common traits in plant functional ecology don’t seem to be important in terms of trait x environment interactions (e.g., SLA). Yet when I speak to other scientists, they want to know what these common traits are doing. It seems like unless you have a result that is very impressive, you can only deviate away from what’s expected in little, incremental steps. Second, perhaps this is naive, but I wonder how much of the “bandwagon” effect is driven by the expansion of a new research area, and thus the attraction of untapped potential, and less because it’s cheap and easy.
Interesting questions. I definitely think part of the bandwagon is it builds a momentum all of its own (or really of course because of the riders as you say). You are also of course right that there are good reasons for people to go into functional traits. I did it myself!
SLA is an interesting trait. I’ve never been clear myself why we treat it like the most important possible trait.
It would be fun to poll people on what they think the most important possible trait might be. I would vote for size (e.g. height or body mass) over SLA myself.
I 100% agree body size would top my list (and hence thanks for your great paper on plant height across the globe). Its not as often measured or established but I wonder if size of subcomponents (e.g. leaf, seed) and ratios (leaf volume to stem value, root volume to total volume) wouldn’t come next (at least in plants where the components can vary fairly independently).
Thanks a lot for this very nice post. I totally agree and would like to share some thoughts. From my point of view, the previous name of “functional ecology” was ecophysiology. As already identified for studies on community assembly, little regard to history of science lead us to the risk of reinvent ideas. Functional ecology and ecophysiology were even considered as the same discipline, although, in certain situations, researchers may have different research agendas for each. The ability to recognize this divergence may decrease the risk of neglecting ecophysiological studies that are not placed under the label of functional ecology. Recently, I and two colleagues discussed about the importance of ecophysiology to avoid the use of “fashionable traits” from the LES. Fashionable traits are those commonly used based on the popularity and easiness you mentioned, but that do not necessarily hold their ecological meaning across scales. SLA is one of them.
Click to access 2013-28_tcm19-357073.pdf
You raise some interesting points about functional ecology vs ecophysiology. Functional ecology was very popular as I was finishing my PHD ~15 years ago, meaning especially there were many jobs advertised in “functional ecology”. I was never entirely clear on what it was (and indeed many of the candidates for these jobs confessed to not being clear). My understanding is it was an attempt to combine physiology with behavior primarily (i.e. combining under one roof fields at the individual level).
But yes it has never quite worked and so functional continues to have vague meanings and people continue to practice under ecophysiology and behavior.
What is functional trait ecology? If you sit down with the dictionary and try to work it out from the words “trait” and “functional”, then indeed it must seem like almost everything in ecology would be included. Ecophysiology, evolutionary ecology, ecosystem processes, community assembly – all of these have got something to do with traits – does that mean they’ve all now been engulfed into trait ecology?
Rather than setting out formal definitions, for me it makes more sense to think of trait ecology as a movement within the flow of research down the years. The recent enthusiasm for plant species traits got started in the 1990s. It grew out of two problems, mainly. One was “plant functional types” in the vegetation component of global change models – everyone knew the existing PFT-systems were unsatisfactory, but what might be a better solution? The other was the search for an ecological strategy scheme that would make sense of the 300K species out there. The available schemes, notably Grime’s CSR triangle, did a good job of capturing ideas about processes, but you couldn’t use them to compare across different vegetation types. There was no protocol for taking species from Sheffield and Sumatra and San Diego and positioning them relative to each other on a common C-S axis.
So the suggestion to use measurable species traits directly as strategy-dimensions arose as a sort of sidestep. It opened up a path forward, the opportunity to get species comparisons together at world scale. And in those terms it has been working pretty well. Over the past 15-20 yr a much more quantitative picture has gotten built about the breadth of plant ecologies. Arabidopsis and Acer and Araucaria can now be positioned against a trait-constellation, with coverage of tens of thousands of species at least for some traits. We have a much clearer sense of how typical or exceptional particular species are. And the reference trait-constellation is global, spanning across continents and climate zones, and also spanning across the whole phylogenetic tree.
I do totally understand Brian’s sentiment that there are a lot of fairly boring manuscripts around that involve measuring plant traits. And yet, isn’t there something at least a little bit heartening about people being willing to contribute with an eye to building a collaborative world-scale picture? There’s a communitarian impulse at work. Let’s give it a kind word or two, as well as making lists of deficiencies.
But anyhow, coming back to plant strategy ecology taking a sidestep during the 1990s to using measurable species traits for graph-axes. As sidesteps do, this opened up running room in some directions but at the same time dodged issues in other directions. (One dodged issue was the mechanisms for how species interact and species mixtures get assembled. Another was the mechanisms behind species boundaries along climate gradients.) If people expected traits to solve all the problems in ecology, then it’s no surprise they’re feeling disappointed two decades later.
Brian provides a list of nine directions for trait ecology. Definitions need tightening, variances are important, sometimes the traits we have aren’t the ones we really want, reality is multidimensional, there are different scales of interest. All true enough.
But going back to Brian’s bandwagon metaphor, I’m not personally very convinced that finger-wagging the band about definitions and methodology is going to make the music go with a swing. Seems to me that researchers need to identify what process it is that they want to understand, or what prediction they want to make, or what sort of descriptive picture they want to paint about the world’s ecology. It’s the research question that decides whether a particular source of variance or hierarchy of categories is important for the purpose.
Perhaps it could be productive if a strand within this discussion were to occupy itself with what questions people personally want to answer (and why they think species traits might help with that). That might help to clarify the question what trait ecology is up to currently, and whether it’s at all useful to think of it as a single movement any longer.
Thanks for dropping by Mark!. A very useful summary of the history.
I really like your point about identifying questions. I think this is central to moving forward.
For me the two questions I am most interested in answering with traits are:
1) Understanding how communities assembly (and a belief that traits provides a useful alternative lens to one focused on species) (per our joint paper in TREE in 2006)
2) Understanding the patterns of variation in biodiversity out there across larges scales in space and time (again through a lens that is hopefully informative in addition to/instead of the species lens).
OK good, so here are a couple of questions that I’m interested in:
1. When we have case studies covering (say) 6 Piper species, or 4 Banksia species, or two Helianthus species, how widely do we expect conclusions from those studies to apply across the plant world? This is trait ecology to the extent that indicator traits might offer a pathway to an answer. Maybe it’s worth noting also that this question doesn’t supersede physiological or functional ecology – the in-depth work on small numbers of species is still important in its own right – the trait ecology works hand in hand with the physiology.
2. What are the rules for assembling species mixtures in natural vegetation (given that at most sites there are far fewer species than could potentially be cultivated there, but usually several species rather than a single winner)? I’m interested in an answer expressed as a trait-mixture, the constellation of properties of the species, more so than an answer expressed as number of species.
Dear Brian and Mark, thanks for the nice post and comments!
About the search for an ecological strategy scheme that would make sense globally, commented by Mark, I think we could not forget some old theory of plant adaptive strategies, like Grime’s CSR theory, that consider how strategies have evolved and why some strategies occurs consistently in some environmental/ecological situations. Otherwise, we can see and ameliorate them from measurable traits, and use them to compare ecological processes across different vegetation types, using a global classification system. About the CSR theory, for example, despite some negative reviews, it seems to me that it is not just applicable to Sheffield. Here in Brazil and in Italy, for example, the floras has the same triple trade-off, so it seems to me a strong evolutionary constraint. Attempts to draw up a classification protocol were initially frustrating, but now there is a simple classification method that is being improved from global data bases: http://onlinelibrary.wiley.com/doi/10.1111/1365-2435.12095/pdf
Just to point out.
All the best!
Interesting points and discussion Brian! Very much enjoyed the read. I think that it has a lot to do with scale as you mentioned. In terms of the science I will need some time to think about that…but as to the phenomena of the bandwagon I tend to disagree slightly. While I am sure there are some “lazy” or sensation chasers out there I also think that the bandwagon as you call it is important. A few years ago when I was starting my MSc I may have been one of these jumpers but my motivations were very different. I was fascinated by the potential of the field and the ability to tie together quite different ecological components. My first introduction was via Wright’s 2004 Nature paper- which immediately captured my attention and led me to my MSc. I see and agree with some of the shortcomings you mentioned but my point is that bandwagons have a place because they may inspire greater interest in a field and compel a large group of people to work in it (regardless of whether these people stick around or not)- which in my opinion is only a good thing.
I have seen mention of boring functional trait studies or studies simply measuring a number of traits in a single system on a few species. These have their place. I like to think of basic science as the “raw material” for more complex meta-analyses which then expand the field. Do you not think that this poor view of studies simply measuring traits is an artefact of the publishing culture as a whole? where exciting, catchy or field-advancing studies are highly encouraged while often the studies which capture the basic data and/or make comparisons are less so? What do you think studies such as this could do to improve the field as a whole?
I would be very interested to hear your thoughts on this.
Thanks for the great blog!
Thanks for commenting. I agree (and hope it was clear from my post) that a bandwagon cuts two ways. It is not all bad. To my mind (and indeed as I hinted in the title) – the challenge is to try to make the bandwagon phase as productive as possible – not to eliminate it (which I doubt is a realistic goal anyway).
You raise some important points about measuring a bunch of traits being an important part of the process (I think of it as adding a brick to the wall of science). When that turns into papers and whether it is a good paper or not probably says a lot about our publish and perish culture these days.
Well lets hope the end bit of the bandwagon phase is more successful!
I agree that it does say a lot about that culture. I am very much against publishing poor quality papers simply for the sake of publishing. Maybe a solution is for these kinds of studies to be collecting data to fill an identified gap?
@Jessica Light (below; sorry, messed up the threading):
Not sure if this quite counts in your eyes, but have a look at Brian’s cv:
Brian’s been hired three times as a tenure-track ecologist, not statistical consultant (McGill, moved to Arizona, moved to Maine). He’s done some theoretical work, and has some conceptual/commentary/opinion pieces that have been quite influential. But I’d say that what he’s mostly known for, and has mostly been hired for, are analyses of data he didn’t collect himself. Hardly anything on his cv is based on data he (or his students) collected themselves.
Could I pick up on your point about studies that capture basic data? — because I think it’s a really important one. One thing people fret about in trait ecology currently is that a lot of projects are built round synthesizing or meta-analysing existing data. But it will be a big problem if ecology’s reward system ever gets to a point where you no longer get career-credit for doing the hard work in the field.
This issue intersects with questions about open access to data. As you’ll know, there’s considerable debate about how to handle data ownership, the circumstances where it will entitle you to authorship, and so forth. And it’s a fast-changing situation. Datasets without any narrative attached can now have citable doi-s, and “data papers” are becoming more common in journals. Soon it’ll be theoretically possible to become highly-cited on the strength of datasets rather than of papers. And I personally think that’ll be a good thing. If you’re perceptive enough to identify critical data that lots of people really need, and skilled and hard-working enough to collect data that can be trusted, then you absolutely should be seen as one of the leaders of the field.
But we’re not there yet. I’ve yet to see anyone get a tenure-track position, much less a senior one, on the strength of data contributions alone. I think it’s one of the big questions for ecology over the next 20 years or so — what sort of work do we want to reward or praise most highly?
Very good point Mark! I agree that it is a fantastic thing that datasets are becoming citable. The point you raise about what sort of work do we want to reward is important indeed. I must admit that I am only just beginning with my PhD and so I am not very well acquainted with the politics behind publishing (although I am in the process of preparing a manuscript- which includes functional trait data) and in academia in general which makes these sorts of discussions even more interesting to me- especially as I hope to follow a career as an academic.
Thus, based on my limited exposure my feeling is that both the data contribution and data synthesis branches should be praised and rewarded albeit for different reasons. The datasets-as you mentioned should contain critical data that is highly sought after. After all, collecting good, reliable data is not always an easy task. This is why I think global databases such as TRY are wonderful as they fuel both approaches.
“But we’re not there yet. I’ve yet to see anyone get a tenure-track position, much less a senior one, on the strength of data contributions alone.”
— On the flip side, have you seen anyone get (non-statistical consulting) tenure-track positions based solely on meta-analyses or works on others’ extant data sets?
Late to this post, and its awesome. Of course I only comment with a criticism, but I hope its constructive!
Condition 1 basically excludes any application of trait based ecology to microbial life. The best you could do is measure a trait on clones of the same individual in a plate. I don’t think this is your intention, and I don’t think it needs to be so strict.
Second, Condition 1 seems to ignore the potential role of neutral biodiversity allowing you to extend the measurement of a trait across a functional group, as memebers within that group are essentially equivalent. We can talk microbes or tropical trees or whatever, but many organisms are doing similar things in the environment, and it can be useful to extend trait based ecology to the functional group. I would argue this approach needs to be taken if you are serious about using trait based ecology to actually understand ecosystem ecology.
“the potential role of neutral biodiversity ”
Where’s the evidence that, say, lots of different species of tropical trees have dynamics dominated by neutral drift?
Valid enough point about microbial ecology. I guess I would just amend my claim to say “conceptually could be measured on one individual” – I do not think intrinsic rate of population increase or population mortality rate is a trait. Important numbers yes, but not a trait.
I know functional groups play an important role in microbial ecology. They are important in dominant plants (i.e. mostly trees) for some people, but not for others. I guess whether talking about a trait of a whole group of species is valid/useful depends on your question which gets back to Mark’s point.
However, I do NOT see neutral biodiversity as an argument for taking a trait of a whole group of species. Indeed, neutral biodiversity is basically anti-trait – no trait matters – not a claim that all species have the same trait.
Thanks for the reply. My comments on neutral biodiversity aside, How would you compare trait based and functional group based approaches for understanding community assembly and ecosystem function? Are they really fundamentally different approaches, or are they each extensions of the other? One considers traits at the individual and species level, the other across multiple species executing similar roles in the environment (i.e. photosynthesis, decomposition of lignin, nitrification, etc.) Is studying and characterizing functional groups within an ecosystem (rather than species or individuals) a version of trait based ecology, or completely different?
Hi Colin – to me I think of this as ‘taxonomic scale’ – are you studying units of individuals, species, or sets of species. I think all are valid. They just depend on your question.
In the botany trait world, function groups are mostly used for predicting biosphere impacts on global dynamics models (carbon uptake, moisture release etc). For these models some broad functional groups like broad-leafed deciduous vs needle-leaved evergreen and C3 vs C4 grass are useful. For the questions I’m interested in about community assembly and even quantifying biological variation (aka biodiversity) I think functional groups are not so useful.
I know for microbes functional groups are often based on things like which substrate is used for energy and cell wall structure. I think these are almost an analog for the class and phyla level in larger ecology (e.g. birds vs mammals) or at least order (carnivora vs artiodactyl). As such, I think this is very much in the spirit of what motivates traits for me – trying to be functional rather than taxonomic in organizing diversity – it is just organizing diversity across a much broader sweep of life’s evolutionary history than most ecologists attempt to do and thus naturally higher level.
The first thing I always want to see with any “functional group”-based analysis is evidence that the groupings have some biological reality. That evidence often isn’t there, and finding it often is trickier than it seems. For instance, in the context of BDEF research, standard ways of sorting plants into “functional groups” have no more explanatory power than random groupings. It’s the mere lumping of species into groups that creates the appearance of explanatory power for “functional groups”:
Petchey 2004 Functional Ecology: http://onlinelibrary.wiley.com/doi/10.1111/j.0269-8463.2004.00852.x/full
Wright et al. 2006 Ecology Letters: http://onlinelibrary.wiley.com/doi/10.1111/j.1461-0248.2005.00850.x/abstract
Thanks for interesting post and discussions – I hadn’t realised that functional traits were a bandwagon before reading this so will be more wary of flinging that term around willy-nilly!
I don’t usually do any blogging but this peaked my interest.
I wanted to mention an area where functional traits are gaining momentum arguably out of necessity rather than for more academic reasons. It would be a small part of the overall literature but thought it interesting to add an applied example.
The restoration ecology community in Australia is faced with the two compounding problems of widespread degraded agricultural systems where perennial vegetation needs to be re-planted, and climate change predictions that suggest that by the end of the century most of Australia’s biomes will be completely different from what they are now (e.g. E.g. Fig 7, Fig 10 in https://publications.csiro.au/rpr/download?pid=csiro:EP105380&dsid=DS4). So while up until a few years ago restoration ecologists and practitioners were concerned with maintaining local adaptation by only sourcing seeds and seedlings from strict local provenances (e.g. sourced within 20 km of a site) increasingly workers are asking:
1. What do we plant if we are planting trees that will live for 300 years by which time the climate will be completely different? Should we be planting from species or populations from further afield from more arid regions within Australia that might have functional traits that could allow them to be better suited to future climates? (e.g. http://onlinelibrary.wiley.com/doi/10.1111/aec.12122/abstract). Potentially this is putting into practice Brian’s point #7 by trying to find individuals with the trait of interest rather than only looking at the species level (?).
2. In 100 years time it might be the case that many local species will no longer survive the changed conditions, in which case, should we cease to worry about the native/exotic divide as long as we can get something to grow that provides the functional traits to keep our production systems going? E.g. perenniality of vegetation is considered a climate change adaptation service and can be provided by native or exotic species (Table 1 in http://onlinelibrary.wiley.com/doi/10.1111/gcb.12689/abstract)
So it seems, the concept of functional traits is being applied to help make long term management decisions. I don’t know if this makes the lack of theoretical underpinning around functional traits even more alarming but it does show that even just the concept on its own is driving development of thinking in a related field. So I would also agree that it’s more helpful to try and steer the wagon than jump off it (although I couldn’t exclude the possibility that there is a nested sub-bandwagon within the restoration literature that needs steering too!).
Thanks for taking the time to comment. You raise some interesting examples from the restoration world. As Mark Westoby pointed out in the comments I think the key to steering is to have some clearly focused goals and questions. These are some nice ones.
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Thanks for the post.
(To preface, I’m a public science educator, not a practicing scientist, so I’m driven to find slightly neater answers than the real world can provide.)
This is all fascinating stuff.
Reading the paper you wrote in ’06 and everything here, I see lots of debate about the details, but I can’t seem to find anyone actually implementing the data in a productive way. In the paper, you imply that ecologists can use functional trait data to “make predictive statements to help policy makers make informed decisions.”
I see synthesize and meta-analysis, but when does this turn into action?
Am I missing a step here? This whole debate feels a bit like a cliffhanger.
Perhaps it’s just parties in less academic fields that are utilizing the data (like the comment above)?
Very curious where this all leads!
That would be *synthesis*
Probably I am guilty of discussing this in too much of an an insiders way and not summarizing progress in the trait world. But its definitely out there.
Bill Shipley’s 2008 paper predicts abundance from traits.
Daniel Laughlin has several papers (he calls it he TRAITSPACE model)
Eric Garnier has a new book on traits that is very nice
The recent work led by Sandra Diaz on calculating the major axes of variation in traits
A paper by Lamanna et al (I’m a coauthor) comparing trait volumes in the tropics and temperate zone (really the whole special issue that appears in)
Peter Reichs speculation about the major trade-offs underlying traits
Angela Molles has some papers measure global variation in important traits (as do Nate Swenson, Ian Wright and others)
Cyrille Violle has a cool paper on traits in agricultural fields
Chris Baralato on really quantifying the best sample strategies for traits
And many more!
Its just a small fraction of the papers being published on traits. Which is what I take as a definition of a bandwagon. But maybe its also just true of scientific research in general.
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Hi Brian, that was a very helpful post. I am a student working on population ecology of corals, there has been increasing number of papers on trait based approach in coral reef ecology as well. But I am confused about a few concepts especially regarding the distinction between traits and performances (I guess the confusion is more specifically between the higher level nodes and the top of the hierarchical tree you have mentioned).
So would reproductive output or fecundity of an individual, be considered as a functional trait or a performance ? Also what about, growth rates or shrinkage rates (corals colonies usually shrink in size because of many factors like disease, mechanical damage etc) measured by tracking individual coral colonies? Can they be considered as a trait or not ? I am thinking that a fitness of an individual (corals in my case) can be broadly shaped by growth rates, reproductive output and their interaction with each other and with local environment, so maybe they can be considered as functional traits ?
Another question, do you think population structure parameters like skewness, kutosis etc be considered as traits, even though they can only be measured at population level? I read another post by Jeremy where he mentions about Litchman-Klausmeier group using parameters of population growth models as traits, that’s why I was wondering about this.
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