Any young ecologist wishing to get a grasp on the most important ecological questions of the century could find no better place to start than the thoughtful compilations of Bill Sutherland and his colleagues in the U.K. (Sutherland et al. 2006; Sutherland et al. 2010; Sutherland et al. 2013). In general none of these questions by itself could be the focus of a thesis which by definition must deal with something concrete in a 2-3 year time frame, but they can serve as an overarching goal for a life in science. In all of these exercises an attempt was made to canvass dozens to hundreds of ecologists mainly from Britain but including many from other parts of the world to suggest and then cull down questions into a feasible framework.

This whole approach is most useful, but the authors recognize there are some limitations on exercises of this type. A particularly crucial limitation is:

“…there was a tendency to pose broad questions rather than the more focussed question we were aiming for. There is a tension between posing broad unanswerable questions and those so narrow that they cease to be perceived as fundamental.” (Sutherland et al. 2013, p 60).

I want to focus here on the problems of decomposing broad unanswerable questions in ecology to guide our ecological research in the future. I will discuss here only two of the population ecology questions.

Begin with question 13 on page 61 of Sutherland et al. (2013):

13. How do species and population traits and landscape configuration interact to determine realized dispersal distances?

To translate this into a project we have first to decide on a species to study and specific populations of that species. This opens Pandora’s Box because there are many thousands of species and we have to pick. We do not pick the species at random, yet we wish to develop a general answer to this question, so right away we are lost in how to translate detailed species and area specific data on movements into a general conclusion. So just for illustration suppose we pick a convenient mammal like the red squirrel of North America. It is territorial and diurnal and can be fitted with GPS collars so that movements can be readily measured, so in a sense it would be considered an ideal species to study to answer question 13, even though it is not a random choice. It ranges from Alaska to Labrador down to Arizona and North Carolina. There are a variety of landscapes throughout this geographic range, some highly altered by humans, some not. I do not know how many intensive studies of red squirrels are being or have been carried out. I would wager that the entire NSF (or NSERC, or ARC) budget could be spent to set up a series of studies of duration 5-20 years to gather these data throughout the range of this species. Clearly this will never be done, and we can only hope that the results of a few specific studies in non-randomly chosen areas over shorter time periods will answer question 13 for this one species.

Landscape configuration alone boggles my mind. It is in many areas an historical artifact of fire or human occupation and land use, and yet we need principles to generalize about it. We can model it and pretend that our models mimic reality without the availability of an experimental test. Is this the ecology of the future?

Another way to answer question 13 is to use tiny organisms like insects that we can replicate readily in small areas at minimal cost. Such studies are useful but again I am not sure they will provide a general answer to question 13. These studies can provide insights about specific insects in specific communities and with a good number of such studies on a variety of systems perhaps we would be in a position to achieve some generality. Otherwise we could be accused of “stamp collecting”.

Question 14 (Sutherland et al. 2013 page 61) has similar problems to question 13 but is more tractable I think.

14 What is the heritability/genetic basis of dispersal and movement behaviour?

This is a simpler question, given modern genetics, and can be answered for a particular species in a particular ecosystem. It is restrictive, if it is a field study, in allowing only those species that do not disperse beyond the detection range of the equipment used, and in requiring long-term genetic paternity data to estimate heritability. The methods are available but have so far been used on few species in very specific areas (e.g. superb fairy wrens in a Botanical Garden, Double et al. 2005). It is an important question to ask and answer but again the generality of the results at the present time have to be assumed rather than measured by replicated studies.

The bottom line is that questions like these two have been with ecologists for some years now and have been answered in some detail only in a few vertebrate species in very specific locations. How we generalize these results is an open question even with modern technology.

Double, M.C., Peakall, R., Beck, N.R., and Cockburn, A. 2005. Dispersal, philopatry, and infidelity: dissecting local genetic structure in superb fairy-wrens (Malurus cyaneus). Evolution 59(3): 625-635.

Sutherland, W.J. et al. 2006. The identification of 100 ecological questions of high policy relevance in the UK. Journal of Applied Ecology 43(4): 617-627. doi:10.1111/j.1365-2664.2006.01188.x.

Sutherland, W.J.et al. 2010. A horizon scan of global conservation issues for 2010. Trends in Ecology & Evolution 25(1): 1-7.

Sutherland, W.J. 2013. Identification of 100 fundamental ecological questions. Journal of Ecology 101(1): 58-67. doi:10.1111/1365-2745.12025.