There is a most interesting paper that you should read about the important questions in ecology:
Sutherland, W.J. et al. (2013) Identification of 100 fundamental ecological questions. Journal of Ecology, 101, 58-67.
This paper represents the views of 388 ecologists who culled through all of the 754 questions submitted and vetted in a two day workshop in London in April 2012. There are many thesis topics highlighted in this list and it gives a good overview of what many ecologists think is important. But there are some problems with this approach that you might wish to consider after you read this paper.
We can begin with a relatively trivial point. The title indicates that it will discuss ‘fundamental’ questions in ecology but the Summary changes this to ‘important’ questions. To be sure the authors recognize that what we now think is ‘important’ may be judged in the future to be less than important, so in a sense they recognize this problem. ‘Important’ is not an operational word in science, and consequently it is always a focus for endless argument. But let us not get involved with semantics and look at the actual 100 questions.
As I read the paper I was reminded of the discussion in Peters (1991, p. 13) who had the audacity to point out that academic ecologists thrived on unanswerable questions. In particular Peters (1991) focused on ‘why’ questions as being high on the list of unanswerable ones, and it is good to see that there are only 2 questions out of 100 that have a ‘why’ in them. Most of the questions posed are ‘how’ questions (about 65 instances) and ‘what’ questions (about 52 instances).
In framing questions in any science there is a fine line in the continuum of very broad questions that define an agenda and at the other extreme to very specific questions about one species or community. With very broad questions there will never be a clear point at which we can say that we have answered that question so we can move on. With very specific questions we can answer them experimentally and move on. So where do we cut the cake of questions? Most of these 100 questions are very broad and so they both illuminate and frustrate me because they cannot be answered without making them more specific.
Let me go over just one example. Question 11 What are the evolutionary and ecological mechanisms that govern species’ range margins? First, we might note that this question goes back at least 138 years to Alfred Wallace (1876, The Geographical Distribution of Animals), and has been repeated in many ecology textbooks ever since. There are few organisms for which it has been answered and very much speculation about it. At the moment the ecological mechanism in favour is ‘climate’. This is a question that can be answered ecologically only for particular species, and cannot be answered in real (human) time for the evolutionary mechanisms. Consequently it is an area rife for correlational ecology whose conclusions could possibly be tested in a hundred years if not longer. All of these problems should not stand in the way of doing studies on range margins, and there are many hundreds of papers that attest to this conclusion. My question is when will we know that we have answered this question, and my answer is never. We can in some cases use paleoecology to get at these issues, and then extrapolate that the future will be like the past, a most dubious assumption. My concern is that if we have not answered this question in 138 years, what is the hope that we will answer it now?
It is good to be optimistic about the future development of ecological science. Perhaps I have picked a poor example from the list of 100 questions, and my concern is that in this case at least this is not a question that I would suggest to a new PhD student. Still I am glad to have this list set out so clearly and perhaps the next step would be to write a synthesis paper on each of the 100 topics and discuss how much progress has been made on that particular issue, and what exactly we might do to answer the question more rapidly. How can we avoid in ecology what Cox (2007) called a “yawning abyss of vacuous generalities”?
Cox, D. R. (2007) Applied statistics: A review. Annals of Applied Statistics, 1, 1-16.
Peters, R. H. (1991) A Critique for Ecology, Cambridge University Press, Cambridge, England.
Sutherland, W. J., Freckleton, R. P., Godfray, H. C. J., Beissinger, S. R., Benton, T., Cameron, D. D., Carmel, Y., Coomes, D. A., Coulson, T., Emmerson, M. C., Hails, R. S., Hays, G. C., Hodgson, D. J., Hutchings, M. J., Johnson, D., Jones, J. P. G., Keeling, M. J., Kokko, H., Kunin, W. E. & Lambin, X. (2013) Identification of 100 fundamental ecological questions. Journal of Ecology, 101, 58-67.