What are important directions for ecology?

I was recently asked “what is the most important problem in ecology?”. I was dissatisfied with whatever I ended up answering, so it has been on my mind. I think there is an analogy with medicine here – it’s a little like asking a medical scientist “what is the most important disease to cure?” Similarly, there are multiple possible answers, and the one you give will depend on your area of interest/what type of doctor you are. (I also assume this is a question about basic research, and the answer is not as simple as saying, stop extinctions or prevent habitat loss).

Levels of biological organisation.

The medical analogy breaks down a little because ecology is *far* more complicated than medical science. Medicine has a foundation in anatomy and physiology, which in turn rely on basic sciences like cell biology and genetics. This creates a reasonably constrained framework within which further learning/investigation can be organized. Medicine typically stops at the level of the individual, but ecology inherently involves many additional levels of organization (from individuals, to populations, to species and communities, to ecosystems, and beyond). Within any one of these higher levels of organization (population, community, ecosystem), there can be such an immense amount of variation in outcomes and dynamics that ecologists can lose sight of connections with lower and higher levels. For example, community ecology encompasses so much complexity on its own, that also considering the impacts of population level processes and on ecosystem level processes is a tall order. But, we should also appreciate, given these barriers to understanding, just how far ecology has actually advanced in the last 100 years. The combination of reductionist experiments and descriptive work at all scales has been immensely successful (e.g. see this blog post for a partial list). Many general tools have been developed that we can then use to answer specific ecological questions (the integration with statistics with ecology has been highly successful; the use of specific mathematical models). Still, the ability to reconcile multiple levels of organization and scales still limits ecology.

This is a problem that cell biology has also experienced, and is now approaching via systems biology: "The reductionist approach has successfully identified most of the components and many of the interactions but, unfortunately, offers no convincing concepts or methods to understand how system properties emerge...the pluralism of causes and effects in biological networks is better addressed by observing, through quantitative measures, multiple components simultaneously and by rigorous data integration with mathematical models"(1): to me, this quote rings so true for ecology as well. Systems biology uses mechanistic, mathematical and computational models to attempt to represent multi-scale complexity.

Of course, the optimism about systems biology might be premature in that it hasn’t produced many useful models yet, such that it may be “more of an agenda than a body of results.”. Some of the best “systems ecology” (e.g. meta-ecosystem models) are very system specific and data-heavy (e.g. 2). Can they inform us about generality in ecology?

All of which is to say, I think the most important problems in ecology relate to this need to make the connections between studies and systems and levels of organization. But, doing so may be difficult.

More specific problems

1. The scaling of ecological processes. Many ecologists include a line about being ‘interested in questions of scale’ on their website blurbs. Despite this, our understanding of the aggregate outcome of multiple processes that are occurring at different spatial or temporal scales remains limited, and poorly predictive. There have been a few useful starts (particularly in Peter Chesson’s scale transition papers (3, 4)), but recent theoretical interest seems to be low. We have data at the community scale, and data at the macro-scale. How do we connect these (and can we)? Models describing how processes occurring at smaller scales produce larger scale dynamics can be complex: they may include non-linearities, autocorrelation between regions, the combination of discrete and continuous events, and multiple attractors.

2. Mechanisms maintaining multi-species coexistence in the real world. Hutchinson’s paradox of the plankton remains unsolved*. Community ecologists have invested a lot of time and energy into understanding species interactions as seen in natural communities. To explore the mechanisms behind coexistence, usually (but not always) ecologists have focused on two-species interactions (or maybe 3): understanding coexistence in larger groups tends to be mostly restricted to theory. But fitting the individual pieces into the larger puzzle is exponentially more difficult: in observed large groups of interacting species, what is the relative contribution of the many coexistence mechanisms identified? Which mechanisms are most important, and how do they change through space and time?

*Perhaps not surprisingly, given it is a paradox...

3. Moving farther away from species. In so many ways, focusing on ‘species’ as the unit of measurement is limiting, because ‘species’ is a discrete term and ecology is interested in quantitative measures. Important advances have been made by redefining ecology as the outcome of species traits and species interactions (5). But I think our ability to connect these ideas more closely to species’ multidimensional niches can still improve. In particular, understanding that traits and interactions can change in context-dependent ways (plasticity, ontogeny, environment) will be important (6, 7).

4. Reproducibility of ecological research. This is more of a philosophical question - how do we achieve reproducibility in a science where context-dependence, alternative stable states, chaos and stochasticity all affect results? How do we differentiate between reproducibility (same results under identical conditions) and generality (same results under similar conditions) in results?

References:
1) Sauer, Uwe; Heinemann, Matthias; Zamboni, Nicola. Genetics: Getting Closer to the Whole Picture. Science 316 (5824): 550–551. doi:10.1126/science.1142502. PMID 17463274.

2) Dominique Gravel, Frédéric Guichard, Michel Loreau and Nicolas Mouquet. Source and sink dynamics in meta-ecosystems. Ecology 91(7): 2172-2184.

3) Chesson, Peter. Scale transition theory with special reference to species coexistence in a variable environment. Journal of biological dynamics 3.2-3 (2009): 149-163.

4) Melbourne, Brett A., and Peter Chesson. The scale transition: scaling up population dynamics with field data. Ecology 87.6 (2006): 1478-1488.

5) McGill, Brian J., et al. Rebuilding community ecology from functional traits. Trends in ecology & evolution 21.4 (2006): 178-185.

6) Poisot, T., Canard, E., Mouillot, D., Mouquet, N., Gravel, D. & Jordan, F. (2012) The dissimilarity of species interaction networks. Ecology letters, 15, 1353–61.

7) Siefert, A., Violle, C., Chalmandrier, L., Albert, C.H., Taudiere, A., Fajardo, A., Aarssen, L.W., Baraloto, C., Carlucci, M.B., Cianciaruso, M.V. and L Dantas, V. A global meta‐analysis of the relative extent of intraspecific trait variation in plant communities. Ecology letters 18.12 (2015): 1406-1419.

The devil isn't always in the details: how system properties can inform ecology

Selection on stability across ecological scales. Jonathan J. Borrelli, Stefano Allesina, Priyanga Amarasekare, Roger Arditi, Ivan Chase, John Damuth, Robert D. Holt, Dmitrii O. Logofet, Mark Novak, Rudolf P. Rohr, Axel G. Rossberg, Matthew Spencer, J. Khai Tran, Lev R. Ginzburg. 2015. Trends in Ecology & Evolution, http://dx.doi.org/10.1016/j.tree.2015.05.001.

This paper in TREE  on selection at higher level systems has been on my must-read list since it came out a few weeks ago, and it was worth the wait. It does what the best TREE papers do - makes you think a bit more deeply about a common topic. In this case, it develops an approach to understanding complex ecological systems (communities, ecosystems) that is blind to the details that ecologists often focus on.

The search for generalities and commonalities drives modern ecology. In short (though this paper deserves an in-depth read), this paper argues that we can learn much by considering stability and feasibility in complex ecological systems. That is, we can also study community structure or trophic webs by considered whether specific configurations of the system are stable. This is in contrast to a context-centric study of a system, where the usual list of proximate causes (productivity, niche availability, connectivity, etc, etc) may be used to understand why the system looks as it does.

The authors' premise is that nonadaptive (e.g. unstable) ecological systems will be unfavourable and selected against, and the resulting selective process “can produce many of those recurrent ecological patterns that have been observed in nature over large scales of space and time.” This requires that you accept a few underlying concepts: first, that large scale systems also experience selection (whether one prefers selection be in parentheses is up to the reader), in that unstable systems will be lost at faster rates leading to greater frequency of stable systems; and second, that this process of selection is determined by the properties of the system alone, not the specific conditions ecologists often focus on.

As an illustration, consider four possible food webs depicting intraguild predation that vary in their interaction strengths. All configurations are possible, but A-C are likely to lead to exclusion of the intraguild predator. D is most likely to be stable since the strong interaction between the resource and prey results in negative feedbacks between the densities of all species (i.e. when the resource is low, the prey should also be low, reducing the predator density as well) and thus more likely to be observed in natural systems. 

From Borrelli et al 2015.

A more specific example looks at attack rates and handling times in predator-prey interactions. When stability is considered, it seems that although predator-prey cycles may occur, it should be uncommon to have such extreme oscillations that populations reach dangerously low levels where stochastic extinctions may occur. Data suggests that oscillatory dynamics are less common in predator-prey relationships, but do occur particularly for specialist predator/prey pairings. Theory (Rosenzweig-MacArthur predator-prey models) predict that such pairings should be most stable if prey are weakly self-limited and predators have high attach rates/long handling times. Empirical evidence for this prediction supports it surprisingly well.

From Borrelli et al 2015.

 
Other related approaches consider feasibility across food webs, communities, and ecosystems. A community perspective might consider interactions across all species, perhaps using a network approach. Networks should tend towards formations that are the most stable – e.g. short chains rather than long ones. The commonness of nested network structures may reflect these constraints. 

Such an approach to ecology is not entirely new (Robert May's weak interactions comes to mind). But it provides perhaps the best potential explanation I’ve seen for ‘generality’ focused approaches in ecology, including ecological allometric relationships, macroevolutionary patterns, and network approaches. Macroecological patterns have often captured, rather than tidy linear relationships, occupied versus unoccupied parameter space. Thinking about feasibility as a macroecological ‘mechanism’ for ecological patterns at the system scale might lead to new research directions. 

Community ecology is complicated: revisiting Robert May’s weak interactions

Stefano Allesina & Si Tang. 2012. Stability criteria for complex ecosystems. Nature 483, 205–208 (08 March 2012). doi:10.1038/nature10832.

When it comes to explaining species diversity, Stefano Allesina differs from the traditional approach. Community ecology has long focused on the role of two species interactions in determining coexistence (Lotka-Volterra models, etc), particularly in theory. The question then is whether two species interactions are representative of the interactions that are maintaining the millions of species in the world, and Allesina strongly feels that they are not.

In the paper “Stability criteria for complex ecosystems”, Stephano Allesina and Si Tang revisit and expand on an idea proposed by Robert May in 1972. In his paper “Will a large complex system be stable?” Robert May showed analytically that the probability a large system of interacting species is stable – i.e. will return to equilibrium following perturbation – is a function of the number of species and their average interactions strength. Systems with many species are more likely to be stable when the interactions among species are weak.

May’s paper was necessarily limited by the available mathematics of the time. His approach examined a large community matrix, with a large number of interacting species. The sign and strength of the interactions among species were chosen at random. Stability then could be assessed based on the sign of the eigenvalues of the matrix – if the eigenvalues of the matrix are all negative the system is likely to be stable. Solving for the distribution of the eigenvalues of such a large system relied on the semi-circle law for random matrices, and looking at more realistic matrices, such as those representing predator-prey, mutualistic, or competitive interactions, was not possible in 1972. However, more modern theorems for the distribution of eigenvalues from large matrices allowed Allesina and Tang to reevaluate May’s conclusions and expand them to examine how specific types of interactions affect the stability of complex systems.

Allesina and Tang examined matrices where the interactions among species (sign and strength) were randomly selected, similar to those May analyzed. They also looked at more realistic community matrices, for example matrices in which pairs of species have opposite-signed interactions (+ & -) representing predator prey systems (since the effect of a prey species is positive on its predator, but that predator has a negative effect on its prey). A matrix could also contain pairs of species with interactions of the same sign, creating a system with both competition (- & -) and mutualism (+ & +). When these different types of matrices were analyzed for stability, Allesina and Tang found that there was a hierarchy in which mixed competition/mutualism matrices were the least likely to be stable, random matrices (similar to those May used) are intermediate, and predator–prey matrices were the most likely to be stable (figure below).

When the authors looked at more realistic situations where the mean interaction strength for the matrix wasn’t zero (e.g. so a system could have all competitive or all mutualistic interactions), they found such systems were much less likely to be stable. Similarly, realistic structures based on accepted food web models (cascade or niche type) also resulted in less stable systems.

The authors reexamined May’s results that showed that weak interactions made large systems more likely to be stable. In particular they examined how the distribution of interactions strengths, rather than the mean value alone, affected system stability. In contrast to accepted ideas, they found that when there were many weak interactions, predator-prey systems tended to become less stable, suggesting that weak interactions destabilize predator-prey systems. In contrast, weak interactions tended to stabilize competitive and mutualistic systems. The authors concluded, “Our analysis shows that, all other things being equal, weak interactions can be either stabilizing or destabilizing depending on the type of interactions between species.” 

Approaching diversity and coexistence from the idea of large systems and many weak interactions  flies in the face of how much community ecology is practiced today. For that reason, it wouldn't be surprising if this paper has little influence. Allesina suggests that focusing on two species interactions is ultimately misleading, since if species experience a wide range of interactions that vary in strength and direction, sampling only a single interaction will likely misrepresent the overall distribution of interactions. Even when researchers do carry out experiments with multiple species, finding a result of very weak interactions between species is often interpreted as a failure to elucidate the processes maintaining diversity in the system. That said, Allesina’s work (which is worth reading, few people explain complex ideas so clearly) doesn’t necessarily make itself amenable to being tested or applied to concrete questions. Still, there’s unexplored space between traditional, two-species interactions and systems of weak interactions among many species, and exploring this space could be very fruitful.