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Copyright ©1998 by The Resilience Alliance*

Jeff Houlahan. 1998. Big problems, small science. Conservation Ecology [online] 2(1): R1. Available from the Internet. URL: http://www.consecol.org/vol2/iss1/resp1/


Response to Walters 1997. "Challenges in adaptive management of riparian and coastal ecosystems"

Big Problems, Small Science

Jeff Houlahan


University of Ottawa

Dr. Walters (1997) raises many good questions highlighting the conflict between the large problems that we face in ecology and the small science often used to address them. Despite increasing awareness of the need for answers to these big questions, large-scale research is rare. Some reasons for the scarcity of research at large scales, shortages of money and manpower, are obvious. These problems, however, are exacerbated by a system of reward in science that encourages "safe" research and discourages the kind of collaboration that will be necessary to address big questions.

Attempts to apply results far beyond the scale at which experimental and/or empirical research is done are ubiquitous in ecology. For example, Wedin and Tilman (1996) find that increased nitrogen deposition leads to decreased species richness and carbon storage efficiency in prairie plant communities. Subsequently, conclusions are drawn about potential impacts of nitrogen deposition upon global warming and biodiversity. If nitrogen deposition controls biodiversity and ecosystem processes at all scales in exactly the same manner, then extrapolation is warranted. However, prairie plant communities are structured, in large part, by fire and/or grazing, neither of which was addressed in the Wedin and Tilman experiments. It is reasonable to suspect that these small-scale results are not going to be simply transferable to the landscape level.

Similarly, the relationship between fertility/biomass and species richness in plant communities (Grime 1979, Wisheu and Keddy 1989) has been well studied, albeit almost entirely at the quadrat level. In a recent study looking at ~ 2000 biomass-species richness relationships, only ~ 15% of the studies sampled areas >1 m2 and none sampled areas > 50 m2 (P.A. Keddy and L.H. Fraser, personal communication). From these studies arise sweeping generalizations about the effect that chronic eutrophication from agricultural fertilizer will have on regional species richness. Again, there are difficulties with this kind of extrapolation. Measures of biomass/fertility at the quadrat level are averages of biomass/fertility across the quadrat. This is unlikely to be a problem at such a small scale, but it seems unlikely that the relationship will hold at the large scale, where "within quadrat" biomass/fertility levels are likely to vary widely.

Why so few studies at large scales? I believe that it has less to do with lack of imagination than with overcaution. To paraphrase Dr.Walters, "doing the thing wrong" is more likely to get a paper rejected than "doing the wrong thing." The first question that should be asked when a paper is being reviewed is "Who cares?" If the answer is "No one," or maybe even " Almost no one," the paper should be rejected. Admittedly, this is more a subjective than methodological criterion, but as long as we continue to accept or reject papers strictly on their methodological merits, we encourage "safe" science. That is, we encourage "small" research designed to be powerful, unconfounded, and precise, at the expense of "big" research that may be none of those.

All of this, I believe, points to a major flaw in the way we do science and, more precisely, in the ways in which we reward the doing of science. Scientific research is rarely designed solely to answer our most pressing questions. Because scientific research is designed by individuals, one of its major purposes is to further the careers of those involved. Most scientists do the work, and want to keep doing it , because they love it .... , but research costs money. Thus begins the vicious circle: get published, to get funding, to do research, to get published ... . The result is a competitive system (with scoring based largely on number of publications, weighted for journal prestige) in which too many scientists are chasing too little money.

The call for interdisciplinary collaboration has, justifiably, become more insistent in recent years. That cry, however, has accentuated the silence surrounding the need for intradisciplinary collaboration. One way in which we are going to be able to do large- scale research is to organize loose, international collaborations of researchers (e.g., Reader et al. 1994). Ideally, researchers doing similar work in different parts of the world need to share a common methodology. This would allow integration of independent research results and, thus, conclusions at a larger scale. There are almost no incentives for such standardization of methodology because the effort involved will not increase the publishability of any individual research, and the payoff in extra publications is uncertain.

Even in the case of post hoc synthesis, the competitive nature of scientific research occasionally rears its ugly head. My experience in attempting to obtain amphibian population data sets illustrates the systemic impediments to the sharing of scientific data. I have been pleasantly surprised by the number of researchers who are willing to pass along unpublished data, but I have also encountered several who are reluctant to do so. Those who decline to contribute data generally do so because they are uncomfortable parting with the data until they have reaped the benefits of their labors. I understand and sympathize, but a system in which open dissemination of scientific information is discouraged is not conducive to doing large-scale research.

"Big" science is going to require "big" dollars and "big" manpower. Our best chance of meeting those requirements is to have a true community of ecologists. That community is unlikely to develop under a system that encourages secrecy, data hoarding, and adversarial relationships among ecologists. As long as publications are currency and data are the promissory notes, there will be little incentive for the large-scale collaborations necessary for the science advocated by Dr. Walters.


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Acknowledgments

Thanks to C.S. Holling, P.D. Clarke , C.S. Findlay, and an anonymous reviewer for helpful suggestions on earlier versions of this manuscript.


LITERATURE CITED

Grime, J.P. 1979. Plant strategies and vegetative processes.  Wiley, Chichester, UK.

Reader R.J., S.D. Wilson, J.W. Belcher, I. Wisheu, P.A. Keddy, D. Tilman, E.C. Morris, J. B. Grace, J.B. McGraw, H. Olff, R. Turkington, E. Klein, Y. Leung, B. Shipley, R. van Hulst, M. E. Johansson, C. Nilsson, J. Gurevutch, K. Grigules, and B.E. Beisner. 1994. Plant competition in relation to neighbor biomass: an intercontinental study with Poa pratensis. Ecology  75:1753-1760.

Walters, C. 1997. Challenges in adaptive management of riparian and coastal ecosystems. Conservation Ecology  [online]1(2):1. Available from the Internet. URL: http://www.consecol.org/vol1/iss2/art1

Wedin, D. A., and D. Tilman. 1996. Influence of nitrogen loading and species composition on the carbon balance of grasslands. Science 274 (5293):1720-1723.

Wisheu, I.C., and P.A. Keddy. 1989. Species richness-standing crop relationships along four lakeshore gradients: constraints on the general model. Canadian Journal of Botany 67:1609-1617.


Address of Correspondent:
Jeff Houlahan
362 Templeton Street
Ottawa, Ontario, Canada
K1N 6X9
Phone: 562-5800 ext. 4575
jeffhoul@science.uottawa.ca

*The copyright to this article passed from the Ecological Society of America to the Resilience Alliance on 1 January 2000.

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