|While ecologists have many outlets for technical
papers, there are very few places that we can present interesting thoughts
and opinions. Therefore, NCEAS is initiating an EcoEssay as a forum for
new ecological ideas. NCEAS will invite innovative and synthetic ecological
thinkers to write an essay for these pages two times a year, and then commission
several reviews of the topic.
In addition, we've created an interactive discussion forum that will allow participants to debate the merit of the current EcoEssay and topics that branch from the original propositions. You are invited to respond to any of the emerging themes for this EcoEssay and suggest topics for other EcoEssays. Now, here's the essay...
An Ecological Perspective on the Challenge of Complexity
by James H. Brown
A PROBLEM?I have become increasingly troubled by what I perceive as the lack of fundamental progress in ecology. Between 1955 and 1975, I can identify more than 20 theoretical or empirical studies that substantially changed the discipline. In the last two decades, I have trouble pointing to even a handful of equally important advances . Why is this? More and better-trained people are doing research in ecology than at any time in history. There is an urgent need and considerable funding to apply ecological knowledge to solve pressing environmental problems. There is every reason to believe that contemporary ecologists are just as intelligent, creative, resourceful, and motivated as they were in the past. Indeed, good work is being done, and much of it is "state-of-the-art": rapidly incorporating the latest advances in such areas as computer technology, remote sensing, molecular biological and chemical techniques, and mathematical, statistical, and experimental methods. These studies have provided more and better data on a wide range of ecological phenomena. There has not, however, been comparable conceptual progress in organizing and synthesizing existing information, producing mathematical models that are both realistic and general, and developing a body of ecological theory that can account for both the infinite variety and the universal features of organism-environment relationships.
I assert that this is because ecology is reaching the limits and exposing the inadequacy of the reductionist approach to science that has predominated for the last century. In essence, this approach has endeavored to understand systems by taking them apart, identifying the fundamental components, and working out how they work in isolation or in small subsystems. Coupled with this kind of reductionism has been increasing reliance on a formal hypotheticodeductive experimental method in which a small number of variables are manipulated in an effort to distinguish between alternative hypotheses. This approach to science has been enormously successful. Among other triumphs it revealed the structure of the atom and the molecular basis of inheritance. In ecology it provided invaluable theoretical and empirical insights into how energy and materials flow through ecosystems and how individuals and populations of organisms interact with their abiotic environments and with each other in simple, usually pairwise, combinations. I do not mean to diminish the importance of these accomplishments, or the extent to which the foundational theoretical and empirical studies before the mid-1970's have been strengthened by subsequent research.
I do believe, however, that this approach to science is inadequate to address many important questions. In particular, reductionist/experimental studies of isolated variables and components are not sufficient to understand the organization of complex systems. Knowledge of physical particles has been of limited use in understanding turbulence and weather, and knowledge of the genetic code has led to only modest advances in whole-organism development. Similarly, knowledge of how organisms deal with abiotic stress, forage, and interact has resulted in only limited insight into the structure and dynamics of populations, communities, and ecosystems. Time was wasted and counterproductive arguments were generated by framing complicated questions as simple alternative hypotheses: are populations regulated by density-dependent or density-independent processes? are communities structured by competition, predation, or abiotic stress? is the successional process competitive or facilitative?
The limitations of this kind of reductionism are becoming increasingly apparent. There is an almost unlimited variety of ways that the biotic and abiotic components can be assembled into complex ecological systems, and many variables, both intrinsic and extrinsic, affect the resulting structure and dynamics. Furthermore, because these components interact with each other in different combinations and on varying temporal and spatial scales, the outcomes of these interactions and the behaviors of the entire systems are inherently nonlinear.
Among other things, this means that there are limits to our ability to make certain kinds of ecological predictions. I once believed that with better data and models we would be able to accurately predict, for example, the future abundance of a rodent or plant population on my study site, the long-term population viability of an endangered species, or the relative success and ecological impact of a newly established exotic species. I am now convinced that trying to make such predictions is akin to trying to predict when and from what cause an individual human will die. Even with excellent knowledge of an enormous number of relevant variables (including age, medical and smoking history, cholesterol level, etc.), precise prediction will always be practically impossible. That is because the human body is a complex dynamical system, and its future behavior is a consequence of complicated relationships among many parts and variables, both intrinsic (e.g., carcinogenic effects of tobacco tar on lung cells, deposition of cholesterol in coronary arteries) and extrinsic (e.g., air pollution, automobile accidents). All analogies fail if pushed too far, but the message for ecology is clear: most populations, communities, and ecosystems are at least as complex as a human body. We need to recognize what kinds of ecological phenomena will always be virtually unpredictable, and to convey this message to colleagues, students, managers, policy makers, and lay people.
ONE SOLUTION?Are we, as some have suggested, approaching the end of scientific progress? I think not. I am optimistic that major advances can and will be made - in ecology as well as in other disciplines. I also believe, however, that they are most likely to be made by those who are willing to question traditional approaches and paradigms and to try new ones.
Most importantly, I am confident that there are some very general ecological laws still awaiting discovery. We have one truly general law: what I call the Malthusian-Darwinian dynamic. No one can deny the importance of Darwin's contribution or the subsequent advances added by the "New Synthesis" and more recent studies. But the Malthusian-Darwinian dynamic cannot be the only general law of ecology. Evolution by natural selection is not sufficient to account for several empirical patterns in ecology that are essentially universal. These include: i) the latitudinal, elevational, and other gradients of species diversity; ii) the distribution of commonness and rarity among species; iii) the distribution of species over geographic space and evolutionary time (species-area and species-time relationships); iv) the dynamical organization of the networks of interactions and exchange of energy, materials, and services among species; and v) the influence of body size on organism-environment interaction, life history, and biodiversity. Such universal phenomena presumably reflect the operation of very general laws of nature. They have been known for decades, but there are still no adequate mechanistic theories or models to explain them. So where and how do we look to search for the laws? I suggest a research program that has the following ingredients.
First, it should focus on emergent and general phenomena. By emergent I do not mean to imply anything deep and philosophical about whether the whole is greater than the sum of its parts. Indeed, any real understanding of a whole system must include a knowledge of its components and their interactions. By emergent I simply mean phenomena that are characteristic of the entire system, and can be measured and studied at that level. Thus, for example, biomass, productivity, and species diversity are emergent characteristics of ecosystems. By general I simply mean universal or nearly so. The empirical patterns listed above are examples of such emergent general phenomena. They offer clues to the universal lawlike processes that govern the structure and dynamics of entire complex ecological systems.
Second, the research program should seek to develop and evaluate mechanistic models to explain these phenomena. The first step is to characterize four basic features of the system: i) what are the important components? ii) how do they interact with each other? iii) what are the key variables: measurable parameters that change in regular and interesting ways? and iv) what are the invariants: measurable parameters that do not change? The second step is to posit cause and effect relationships among these four features. The ultimate goal is a formal model in which relationships among state variables are expressed as mathematical functions. Note that such a model requires knowledge of the components and their interactions obtained from reductionist studies, but it focuses on how these parts contribute to emergent features of the whole system.
Third, the model needs to be evaluated empirically. This means assessing its ability to account for existing data and, most importantly, to withstand rigorous tests of its assumptions and predictions. Empirical evaluation requires that the variables in the model be measured practically and accurately. This may seem obvious, but many existing ecological models are expressed in terms of quantities - population carrying capacity, competition coefficient, and food web connectence are three examples - that cannot really be measured. Rarely will an initial modeling effort be able to make supportable predictions. Therefore, the process of model construction and evaluation must be an iterative one, until it produces a formalism that can account for the key features of the system. It is also important to emphasize that every model is an abstraction, a simplified formalism that captures the essence of a more complicated reality. The goal of producing scientific theories and models is not to describe nature in all its detail, but to understand the lawlike mechanisms that maintain the order that underlies the variety. It is essential to understand those mechanisms in order to have a truly predictive science that can guide policy and management.
Finally, models and theories gain support and strength when they interlock to form an integrated conceptual basis for understanding the natural world. Science is itself a complex system in which the various parts are logically interconnected to form a unifying synthetic structure. This means that it is important to seek ecological laws that make explicit connections to other established scientific laws. I believe that there is much opportunity to seek explanations for ecological phenomena in terms of physical laws. All of the general ecological phenomena listed above, including the Malthusian-Darwinian dynamic, are subject to physical laws, most notably chemical stoichiometry, conservation of mass and energy, and thermodynamics. It seems desirable to seek explanations for these phenomena that relate their biological features to established physical principles.
AN EXAMPLEI will illustrate the above approach using my own recent research on allometric scaling. Variation in body size is the single most pervasive theme of biodiversity. Organisms vary in body mass by more than 21 orders of magnitude, from 10-13 g microorganisms to 108 g whales. Many ecological characteristics of organisms, including resource use, life span, spatial ambit, population density, and species diversity, vary with size. This variation is characterized a power function, Y = cMb, where Y is the structural or functional biological variable of interest, M is body mass, c is a constant that takes on particular values depending on the dependent variable and the kind of organism, and b is the allometric exponent, another constant. G.B. West, B.J. Enquist, and I have developed a model to explain the origin of these universal scaling laws (Science 276:122-126, 1997). We began with an emergent phenomenon: that b typically is some multiple of 1/4 (e.g., 1/4, 3/4, 3/8, or 1) rather than a multiple of 1/3 (e.g., 1/3, 2/3, or 1) as would be expected from simple geometric considerations. Thus, for example, the metabolic rates of animals and the cross-sectional areas of mammalian aortas and tree trunks scale as the 3/4 power of body mass. We assumed that metabolic rates and other fundamental characteristics of organisms are ultimately limited by the rate at which essential resources are transported through the networks of linear tubes that supply the body. We further assumed that these networks: i) branch to reach all parts of the three-dimensional body, ii) minimize the energy required to distribute materials, and iii) have terminal branches (e.g., capillaries in mammalian vascular systems) that do not vary with body size. These assumptions were incorporated into a mathematical model that predicts the design of a space-filling fractal network that minimizes hydrodynamic resistance.
The modeling exercise illustrates the features of a research program as outlined above: 1) focus on emergent, whole system phenomena: the ubiquity of quarter-power scaling relationships; 2) production of a mechanistic model that characterizes the components (anatomical parts of the distribution system), interactions (physical connections and hydrodynamics), variables (dimensions of the components and hydrodynamics of the fluids), and invariants (size of the terminal tubes) of the system, and then derives mathematical functions that describe the mechanistic relationships among the state variables; 3) empirical evaluation: the model predicts the 3/4-power scaling of metabolic rate and scaling relationships for structural and functional characteristics of mammalian cardiovascular and respiratory systems, plant vascular systems, and insect tracheal tubes. 4) connections to other scientific laws: the model incorporates hydrodynamic principles (Poiseuille's law, Navier-Stokes equations) and fractal geometry.
Most importantly the model seemingly accounts for the fundamental features of a complex system: the structural design and hydrodynamic function of the entire distribution network. The general model is highly simplified, and it must be modified to take into account characteristics of specific systems, such as the pulsatile flow of blood of vertebrates or the vessel bundle structure of plant vascular systems. It seems to be able to explain many of the anatomical and physiological features of individual organisms. It remains to be seen whether the model can be extended to understand the ecological scaling relationships that stimulated our collaboration. Nevertheless, it illustrates how we can make progress in discovering the lawlike processes that govern the structure and dynamics of complex systems. Allometric scaling of metabolic rate has much in common with the nearly universal ecological phenomena listed above. It is an emergent feature of complex systems (individual organisms) that has puzzled biologists for decades.
IN CONCLUSIONI close with a few words of qualification. This essay is a musing, not a manifesto. It is a personal assessment of the present state and future prospects of ecology. It is not a call for abandonment of the traditional reductionist, hypotheticodeductive, experimental approaches to science. These still have their place, and, indeed, I am avidly continuing my ecological experiments in the Chihuahuan Desert. The essay is, however, an unabashed effort to encourage those who would try new approaches to discover the laws that govern the structure and dynamics of individuals, populations, communities, and ecosystems.
Although I believe that major conceptual breakthroughs in ecology are possible, they will not come easily. In the present climate of intense competition for limited journal space, grant funds, and jobs, scientists - especially young ones - are inclined to tackle small, safe problems rather than big, risky ones. The peer-review process tends to reinforce this conservativism. Cultural and institutional changes are needed. NCEAS, with its mission to advance synthetic research, can potentially play a key role. It can promote development of models and theory. The ultimate scientific synthesis is a general law that provides a mechanistic explanation for many diverse empirical observations. NCEAS can foster collaborative research. The views expressed above have been powerfully influenced by collaboration with two physicists, G.B. West and F.A. Hopf, whose knowledge of physical laws and mathematical techniques enabled us to tackle problems that I could never have addressed on my own.
In many ways ecology epitomizes the challenge to contemporary science. We could better solve the environmental problems facing humanity if we could discover additional laws of nature that underlie the complexity of ecological systems. We have enormous resources of new information as well as previous conceptual and empirical advances to draw upon. I cannot imagine a more exciting time to be an ecologist!
Jim Brown is a Regents' Professor in the Department of Biology, University of New Mexico, Albuquerque, NM 87131 and an External Faculty Member of the Santa Fe Institute, 1399 Hyde Park Road, Santa Fe, NM 87501. The ideas expressed above have developed over a 30-year career as a result of interactions with many colleagues and students.
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