Category Archives: Ecological Bandwagons

On Important Questions in Ecology

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.

Two Visions of Ecological Research

Let us assume for the moment that the goal of scientific ecology is to understand the reasons for changes in the distribution and abundance of animals, plants, and microbes. If you do not think this is our main agenda, perhaps you should not read further.

The conventional, old paradigm to achieve this goal is to obtain a good description of the natural history of the organisms of interest in a population or community, define the food web they operate within, and then determine by observations or manipulations the parameters that limit its distribution and abundance. This can be difficult to achieve in rich food webs with many species, and in systems in which the species are not yet taxonomically described, and particularly in microbe communities. Consequently a prerequisite of this paradigm is to have good taxonomy and to be able to recognize species X versus species Y. A whole variety of techniques can be used for this taxonomy, including morphology (the traditional approach) and genetics. Using this approach ecologists over the past 90 years have made much progress in deriving some tentative explanations for the changes that occur in populations and communities. If there has been a problem with this approach, it is largely because of disagreements about what data are sufficient to test hypothesis X, and whether the results of manipulation Y are convincing. A great deal of the accumulated data obtained with this approach has been useful to fisheries management, wildlife management, pest control, and agricultural production.

The new metagenomics paradigm, to use one label, suggests that this old approach is not getting us anywhere fast enough for microbial communities, and we need to forget most of this nonsense and get into sequencing, particularly for microbial communities. New improvements in the speed of doing this work makes it feasible. The question I wish to address here is not the validity or the great improvements in genetic analysis, but rather whether or not this approach can replace the conventional old paradigm. I appreciate that if we grab a sample of mud, water, or the bugs in an insect trap and grind it all up, and run it through these amazing sequencing machines, we get a very great amount of data. We then might try to associate some of these kinds of data with particular ‘species’ and this may well work in groups for which the morphological species are well described. But what do we do about the undescribed sequences? We know that microbial diversity is much higher than what we can currently culture in the laboratory. We can make rules about what to call unknown unit A, unknown unit B, and so on. That is fine, but now what? We are in some sense back where Linnaeus was in 1753 in giving names to plants.

Now comes the difficult bit. Do we just take the metagenomics approach and tack it on to the conventional approach, using unknown A, unknown B, etc. instead of Pseudomonas flavescens or Bacillus licheniformis? We cannot get very far this way because the first thing we need to decide is does unknown A a primary producer or unknown B a decomposer of complex organic molecules? So perhaps this leads us to invent a whole new taxonomy to replace the old one. But perhaps we will go another way to say we will answer questions with the new system like is this pond ecosystem changing in response to global warming or nutrient additions? We can describe many system shifts in DNA-terminology but will we have any knowledge of what they mean or how management might change these trends? We could work all this out in the long term I presume. So I guess my confusion is largely exactly which set of hypotheses are you going to test with the new metagenomics paradigm? I can see a great deal of alpha-descriptive information being captured but I am not sure where to go from there. My challenge to the developers of the new paradigm is to list a set of problems in the Earth’s ecosystems for which this new paradigm could provide better answers more quickly than the old approach.

Microbial ecology is certainly much more difficult to carry out than traditional ecology on macroscopic animals and plants. As such it should be able to use new technology that can improve understanding of the structure and function of microbe communities. All new advances in technology are helpful for solving some ecological problems and should be so used. The suggestion that the conventional approach is out of date should certainly be entertained but in the last 70 years the development of air photos, of radio telemetry, of satellite imagery, of electrophoresis, of simplified chemical analyses, of automated weather stations, and the new possibilities of genetic analysis have been most valuable to solving ecological questions for many of our larger species. But in every case, at every step we should be more careful to ask exactly what questions the new technology can answer. Piling up terabytes of data is not science and could in fact hinder science. We do not wish to validate the Rutherford prediction that our ecological science is “stamp collecting”.

Why I am Bored with Biodiversity and Ecosystem Services

Ecosystem services have become the flavour of the month and already it seems tired and bland.  “Biodiversity must be preserved for its ecosystem services” but making the tie between diversity and services has been elusive and will continue to be so. A body of literature has accumulated on the results of small-scale experiments in which plant diversity is manipulated and some service, let’s say productivity, is monitored. In some cases a relationship is found − more species more productivity; but not always. A rancher who wants to increase the productivity of her rangeland would be more inclined to plant to a monoculture of a highly productive grass. For example the introduced species, Crested Wheat Grass (Agropyron cristatum), was widely used in British Columbia in the early 20th century. Cheat grass (Bromus tectorum), another exotic species (if we are talking about North America) is expanding into rangeland and while it might increase the diversity, it reduces the productivity for forage.

Recently Mark Vellend (TREE 29(3): 138, March 2014) reviewed a book by Donald Maier, “What’s so Good about Biodiversity? A Call for Better Reasoning about Nature’s Value. “(Springer 2012). The take home message of this book is that the biodiversity−ecosystem services rationale for protecting biodiversity does not always hold and more species does not necessarily translate into more food or less disease.  It is time to get rid of platitudes and to confront our biases in a critical manner when it comes to biodiversity.

Further to this topic, in December 2013 the first meeting was held of the budding International Panel on Biodiversity and Ecosystem Services. It will focus on the following topics:

1) Task force on capacity building
2) Task force on indigenous and local knowledge systems
3) Task force on knowledge and data
4) Development of a guide to the production and integration of assessments from and across all levels
5) Assessment on pollination and pollinators associated with food production
6) Methodological assessment on scenario analysis and modeling of biodiversity and ecosystem services
7)  Methodological assessment on the conceptualization of values of biodiversity and nature’s benefits to people
8) Development of a catalogue of policy support tools and methodologies and providing guidance on how further development of such tools and methodologies could be promoted and catalyzed

Given the involvement of 115 countries it will be interesting to track the success of this panel.  Note that pollination and pollinators are identified as a specific ecosystem service. Critical experimental ecologists should be involved if this panel is to be productive in a meaningful way and, if not on the panel, they should track its progress and comment accordingly. Stay tuned for further updates.

Bandwagons in Ecology

Scientists are like most people in their attraction to bandwagons. Often this is good, since some parts of any particular science may move more quickly than others, creating a bandwagon for scientists building a career. But sometimes this is detrimental in diverting efforts and money from one aspect of a science to another. All would be fine if the older parts of a science were thoroughly understood, and the new bandwagon opened up the solutions to critical problems.

So what does all this have to do with ecology? Ecology has been one example of a science beset by one bandwagon after another during the past 50 years. Many of these bandwagons were relatively harmless because they started with the promise to solve all problems and ended up contributing a small bit of understanding to the subject as it matured. I am thinking now of energy flow in the 1950s, systems ecology and density dependence in the 1960s, competition theory in the 1970s, and mathematical modelling from the 1980s onward. Other examples could be added to this list. At the moment we have two bandwagons that deserve some discussion – climate change and evolutionary ecology.

Climate change is one of the three most critical problems of our day and so it is understandable that much is written about it. Consequently it appears on all grant and scholarship applications as a relevant field. The problem is twofold. First of all, we should not take weather, the ecological side of climate, as the universal explanation for everything that is changing without considering alternative hypotheses for change. If the geographical distribution of a species is expanding toward the poles, climate change is only one of several possible reasons for this. The factors limiting geographic ranges are multiple and have been studied less well than any ecologist would like. We need to keep in mind that there are other ecological problems out there that are not directly tied in with climate change, and these need to be pursued as well. If you want an example, consider the problem of biological control of invasive species.

Evolutionary ecology is a second bandwagon and I fear it is tilting the entire focus of ecological research. The reason is quite clear – technological advancements in genetic studies. Much of science is driven by technological advances and that is good, but again it should not mean that we ignore other unresolved problems. In particular evolutionary ecology has the great potential to describe the world in great detail without necessarily adding any critical insights. In many cases it is stamp collecting and it reminds me of the saying that “Nero fiddles while Rome burns”. Should we as ecologists be concerned more about the practical problems of our day, or about simply understanding nature? There is no reason of course not to do both, and different individuals have talents in different areas of science. But some ecologists might feel as I do that ecological questions are poorly served by much of evolutionary ecology. I listen to many evolutionary ecologists telling us that their work is solving some ecological question when it is obvious that this is a leap of faith with little substance.

I think we need to ask as ecologists what are the problems we wish to solve, and if we could ever decide on a list of these problems, we could ask where we currently sit in solving these problems. It causes a great focus of the mind to look at a practical problem and ask what ecologists are doing about it. At the moment I am in the Philippines at the International Rice Research Institute, and I am overwhelmed by the ecological questions that interface with sustainable rice cropping in Southeast Asia, of pests and beneficial animals and plants, of migratory birds, of chemical poisons and their impacts on non-target species, the list goes on. The assumption at the moment seems to be that plant breeding and genetics will conquer all problems, but we ought to have a Plan B to look at the community and ecosystem dynamics that centre on a rice paddy, and how that might interface with the changing varieties of rice that are produced. We would be more humble if we moved away from genetic determinism to consider that there are other issues, currently ignored, that only ecologists can solve.

Bandwagons will always occur in science, but we should be careful that not everyone follows the pied pipers of the moment.