Monthly Archives: September 2013

Experimental Model Systems in Ecology

Ecology progresses slowly when we have to study natural populations or communities. It is expensive to manipulate large units of habitat, and there are two approaches that suggest themselves to alleviate this problem. First, study small areas that can be analysed and manipulated by one or two persons. This can be a useful approach, depending on your question and hypotheses, and I do not discuss this approach here. The second approach is through experimental model systems. Typically this means taking the question or problem into a semi-laboratory system. For aquatic studies it may mean putting large cylinders in a lake (Carpenter 1996). For rodent studies it may mean putting populations into small fenced enclosures. For sake of clarity I will discuss this latter example with which I am familiar.

The key question for all experimental model systems in ecology is to know at what spatial and temporal scale the system works. To gain precision we typically want to conduct our studies within an enclosure of some small size. That is, we wish to study an open system with more precision by converting it to a closed system of some much smaller size. But what size allows the system to operate as an open natural population, in this example of rodents? In a sense we wish to know the shape of this generalized curve:


Assume there is some natural outcome known for the particular study. In the case of small rodents this might be that the population fluctuates in periodic ‘cycles’. The question then is what size of enclosure is needed to observe this same population trend. One simple way of looking at this is to ask for islands, what size of island allows a closed population to fluctuate in ‘cycles’. For this particular problem we know that you cannot observe ‘cycles’ in small rooms in the laboratory or even in 1 ha field enclosures.

Many other examples can be given for this type of question in ecology. For example, we may know that infanticide in a particular species is rare in natural populations. But if we raise the same species in small cages in the laboratory, we may observe infanticide very commonly. We would conclude that this is not the natural state of this system, and thus decide that you could not draw conclusions about the frequency of infanticide by studying it in small cages.

The critical judgement is whether any experimental model system we design will mimic natural processes that occur in open, real world populations or communities. All too often in ecological studies we assume that the size of the enclosure or study area that we are using is “natural” and the conclusions will represent what happens in natural populations or communities. In an ideal world we would examine a series of sizes of our study enclosures to see the best one that mimics natural outcomes. But this cannot always be done for reasons of time and money. In some cases we have no idea what the natural situation is, and in these cases it is most difficult to know if our model system results bear any relationship to reality.

This whole issue is another way of looking at the problem of habitat fragmentation – how small a piece of habitat can we get by with to conserve species X or community Y? These types of conservation questions always involve a temporal as well as a spatial dimension, given the problem of extinction debts (Krauss et al. 2010). In the extreme case we can argue that we can conserve at least some species in zoos, but this is a way of avoiding the main goal of conserving natural environments and processes.

The bottom line is to ask yourself as you are setting up a study using an experimental model system approach whether the process you are investigating can be observed at the spatial and temporal scale you have available. Alternatively it may be important to try to construct the curve shown above for the system of interest. This question is important because some previous studies for any ecological system may have reached invalid conclusions because of a faulty spatial scale of the model system.

Carpenter, S. R. 1996. Microcosm experiments have limited relevance for community and ecosystem ecology. Ecology 77:677-680.

Krauss, J., R. Bommarco, M. Guardiola, R. K. Heikkinen, A. Helm, M. Kuussaari, R. Lindborg, E. Öckinger, M. Pärtel, J. Pino, J. Pöyry, K. M. Raatikainen, A. Sang, C. Stefanescu, T. Teder, M. Zobel, and I. Steffan-Dewenter. 2010. Habitat fragmentation causes immediate and time-delayed biodiversity loss at different trophic levels. Ecology Letters 13:597-605.

In Defence of Hypothesis Testing in Ecology

In two recent scientific meetings I have attended (which must remain nameless to protect the innocent), I have found myself wondering about the state of hypothesis testing in ecological science. I have always assumed that science consists of testing hypotheses, yet I would estimate roughly that 75% of the talks I have been able to attend showed no sign of any hypothesis. I need to qualify that. Some of these studies are completely descriptive – what species of ferns occur in national park X? Much effort now is devoted to sequencing genomes, the ultimate in descriptive biology. This kind of research work can be classified as alpha-biology, basic description which is necessary before any problems can be formulated. In my particular specialty of population cycles in mammals, much descriptive work had to be carried out to recognize the phenomenon of “cycles”. But then the question arises – at what point should we stop simple descriptions of mammal populations rising and falling? Do we need to study the dynamics of every rodent species that exists? Or in genetics, is our objective to sequence the genome of every species on earth? My point is that after we have enough basic description, we should move into hypothesis testing, or asking why some phenomenon occurs, the mechanisms behind the simple observations. The important point here is that we should not have a single hypothesis or explanation for any set of observations but rather several alternative hypotheses. As a simple example, if we find our favourite plant species is declining in abundance, we should not simply try to connect this decline with climatic warming without having a series of alternative explanations with the emphasis that our observations or experiments should be capable of distinguishing among the alternative hypotheses.

The alternative argument is that we do not know enough about ecological systems to set up a series of credible alternative hypotheses. It is quite possible to go on describing events endlessly in science in the hope that some wisdom will emerge. I do not think this is a profitable use of time or money in science. In ecology in particular I would argue that there is not a single question one can ask that cannot be answered by at least 2 or 3 different mechanistic hypotheses. Our job is to articulate these alternatives and to do whatever studies or experiments are needed to distinguish among them. Of course it is always possible that the correct answer is not among the 2 or 3 hypotheses we suggest at the start of an investigation, and this is often why one study leads to a further one. Consequently we cannot accept statements like “I have no idea why this observation has occurred”. Such a statement means you have not thought deeply enough about what you are studying. Ecological surprises certainly occur while we study any particular community or ecosystem, but we know enough now to suggest several possible mechanisms by which any ecological surprise might be generated.

So I think it incumbent on every ecologist to ask (1) what is the problem or question my research is addressing? And (2) what probable mechanisms can be invoked as the cause of this problem or the answer to this question. Vagueness may be a virtue in politics but it is not a virtue in science. And I look forward to future conferences in which every paper specifies a precise hypothesis and alternative hypotheses. Chamberlin (1897) stated the case for multiple hypotheses, Karl Popper (1963) asked very specifically what your hypothesis forbids from happening, and John Platt (1964) pulled it together in a critical paper. There was important work done before the Iphone was invented. Good reading.

Chamberlin, T. C. 1897. The method of multiple working hypotheses. Journal of Geology 5:837-848 (reprinted in Science 148: 754-759 in 1965).

Platt, J. R. 1964. Strong inference. Science 146:347-353.

Popper, K. R. 1963. Conjectures and Refutations: The Growth of Scientific Knowledge. Routledge and Kegan Paul, London.