12.1 A range of viewpoints on theory

A wide range of opinions exists regarding the use of, and usefulness of, competition theory, and of theory in ecology and evolution more broadly. This opening section will explore three diverse statements about this body of theory, all of which are all closely related to the themes of this book:

Few ecologists are interested now in these misleading equations [Lotka-Volterra models], but mathematicians dote on them and are always trying to foist them off on us—a classic case of the drunkard who loses his watch in the dark but looks for it under the lamp post because that's where the light is.

—Levandowsky 1976, p. 418 Population ecology as a scientific enterprise... is peppered with hypotheses that are not testable and theories that lack or have, at best, weak explanatory relevance.

—Getz 1998, p. 540

...our history of succumbing to enthusiasms is a deep-seated feature of our scientific culture.... We have little choice but to seek inspiration from gurus of the newest ideas; sometimes they turn out to be partially right. However, we should never believe them without a struggle.

—Houle 1998, p. 1875 The three quotations all express dissatisfaction with theory in ecology and/or evolutionary biology. Each of the statements has some components that are consistent with the arguments in this book, and others that are not. None is specifically aimed at competition theory; Levandowsky was referring primarily to Lotkas and Volterra’s independently proposed predator-prey model. However all of the quotations reflect ideas that are important for understanding the recent history of competition theory.

Levandowsky rightly highlights the combination of popularity and inadequacy with regard to the approach taken by Lotka and Volterra (LV). Ifhe were writing today (46 years later), and were writing about competition, he would be at least partially justified in repeating the same statement.

However, it is not mathematicians who are primarily at fault for the continuing popularity of the LV model. Blame must be shared among many parties, and a big share of the responsibility rests with

Competition Theory in Ecology. Peter A. Abrams, Oxford University Press. © Peter A. Abrams (2022).

DOI: 10.1093∕oso∕9780192895523.003.0012 authors of ecology textbooks. Virtually all modern textbooks focus their treatment of competition theory on the LV model. If they mention other models they usually fail to note their inconsistencies with LV What has changed since Levandowsky wrote the above statement is that a large body of literature has demonstrated the inability of the Lotka-Volterra model to adequately reflect the consequences of shared resource use. Despite the fact that many of the articles that demonstrated this inability had appeared before the mid-1980s, the LV continues to be the most commonly used model for theoretical studies of multi-species competition and for studies of evolutionary responses to competition.

Getz (1998) was certainly correct in implying that the scientific enterprise needs to have some predictive ability to be useful. However, understanding any complex natural system requires a number of models of intermediate complexity to reveal what outcomes are possible, and what features might affect the outcome of a perturbation that directly alters one or more components of the system. It is not necessary that each model within this array should be assumed to apply well enough to any single natural system to be used directly for any predictive purpose. Developing a predictive model for a particular system requires that we have a large body of models that include different sets of component elements, so that we have some idea of what subset of those elements might be needed in the model, and which processes might be crucial for the specific prediction. In the case of ecological competition, this body of knowledge was basically stalled at a relatively early stage of development.

If it is resumed, there should be no requirement that each model produced in this process provide better predictions for any specific real-world system or be ‘tested’ on any real set of species before exploring other models that build upon it. And if such a test is carried out, its failure does not mean that the ‘intermediate’ model should be discarded completely. The primary connection to empirical work for these intermediate models is that their component functions should have empirical and/or logical justification. Intermediate models also illuminate aspects of the consumer-resource system that need to be studied further before making a particular prediction (or to improve upon a previous prediction).

Adding more realistic features to a simple model can make some of the predicted dynamics less consistent with natural systems. This does not justify discarding that feature (or set of features) from future models. The development of consumerresource theory provides a useful example, where a modification that is in the direction of increased realism can produce dynamics that are at least arguably less consistent with what is observed. MacArthur’s (1970, 1972) consumer-resource model predicted that competition in 2-species systems never produced cyclic dynamics. Most classically studied laboratory competitive systems are not characterized by cycles. However, MacArthur’s underlying assumption of linear functional responses has since been shown to be unlikely (Jeschke et al. 2002, 2004). Functional responses that saturate with increasing food/resource intake are a logical necessity and are almost universally observed. Holling’s disc equation type II response is the simplest saturating response, and saturation has been observed in a large fraction of laboratory studies. Type II functional responses are associated with instability at low consumer death rates and/or high consumer attack rates in models of predator-prey systems (Rosenzweig and MacArthur 1963).

In many simple models, these cycles are often of such extreme amplitude that they would entail rapid extinction of many real populations. Another empirical problem is that such predator-prey cycles appear to be relatively uncommon (although there is some debate on this; see Kendall et al. 1998). The cycles that have been observed do not have the extreme amplitudes often predicted by the simple model.

These problematic features of models with type II responses do not argue for going back to linear responses in either predator-prey models or models of competition, but rather for modifying the models with type II responses in other ways that reduce instability, and are likely to be present in many systems. Predator-dependence (DeAngelis et al. 1975) of such responses is a mechanism that appears to be very common (Skalski and Gilliam 2001) and has a stabilizing effect. Several other modifications to the Rosenzweig-MacArthur model are known to reduce the probability of cycles, or to eliminate the likelihood of extreme amplitudes; these include stage structure in the prey (Abrams and Walters 1996; Abrams and Quince 2005) and adaptively flexible prey defence behaviour (Abrams 1995). There are a variety of other potential explanations for stabilization, such as direct intraspecific interference in consumers/predators or high levels of immigration of resources/prey. Constructing the predictive models that Getz (1998) calls for a series of models of intermediate complexity incorporating various combinations of these and other features omitted from most extant models.

The third introductory quotation, from Houle (1998), suggests that many of the factors influencing the direction of research have little to do with the ultimate goal of understanding and making predictions about natural systems. Abrupt shifts in the broad topics of primary interest have always been part of the scientific enterprise. And the practice of science is subject to many pressures that have little to do with the optimal advance of knowledge.

It is necessary to obtain funding for research, and such funding for academic fields typically requires projects that can be completed in three to five years. Fundable projects must also have significant novel features. In the case of ecology, most of the practitioners are empirical scientists, for whom theory is often viewed as a means of justifying their own work. However, to be an attractive topic for empirical research, a project must be viewed as addressing a currently popular question, and the results must be achievable within the period of a single research grant or the duration of a graduate student's career. And it usually has to be done with limited funding and space. This is likely to eliminate studies of functional responses involving many species. They would not be viewed as sufficiently novel, as functional responses have been measured many times in the past. These have mainly been measurements of responses to a single resource, so it might seem that a study of responses in a multi-species system could be sufficiently novel to be justified. However, investigating response surfaces when three or more species affect the response is usually not possible given constraints of time, money, and space.

The issues raised by the three opening quotations are explored in more detail in the following sections.

12.2

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Source: Abrams Peter A.. Competition Theory in Ecology. Oxford University Press,2022. — 336 p.. 2022

12.1 A range of viewpoints on theory

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