Understanding our environment has long been central to the scientific enterprise, and is becoming increasingly important as growth in human populations and economic activities intensifies the stresses humans place on the environment. The consequences of those stresses are increasingly evident, such as habitat degradation; the hole in the ozone layer over high latitudes of the Southern Hemisphere; the increased rate of species extinction; changes in various elemental cycles in the soil, the air, and the oceans; and depletion of marine fish populations in many parts of the globe. This is also an exciting and challenging time for the environmental sciences. Progress in knowledge and theory has been stimulated by advances in computing power; in sensing technology below, on, and above the Earth's surface; in techniques and understanding of molecular biology that have increased our ability to understand ecological processes; and many other areas. In addition, there has been growing recognition of the value of multidisciplinary research involving natural and social sciences and engineering. Together these developments have led to a growing awareness of the central importance of the environmental sciences as humankind attempts to transition to a more sustainable relationship with the Earth and its natural resources. Advancing the environmental sciences, then, is both intellectually challenging and essential for the future of humankind. In this context, a key question arises: Of the many topics of great scientific excitement as well as great practical importance, which are the most important and urgent, and which are most likely to yield major results if tackled now? In other words, what are the grand challenges of the environmental sciences? The answer to that question is the topic of this report.
CONTEXT: THE MULTIDISCIPLINARY NATURE OF ENVIRONMENTAL SCIENCE
Most of the major challenges in the environmental sciences (and management) require multidisciplinary 1 solutions. The “environment” may be conceptualized in biological, chemical, physical, or social scientific terms, and important research endeavors arise from all these fields. New training, new organization, and new funding are needed to bring together multidisciplinary teams that can undertake research aimed at understanding the following:
How natural systems 2 work.
How human activities and other influences perturb these systems.
What causes these perturbations.
How changes in one system affect other systems and human well-being.
How the knowledge needed to make well-informed choices about means of transforming or restoring environmental systems can be developed.
Natural systems—ecosystems; oceans; drainage basins, including agricultural systems; the atmosphere; and so on—are not divided along disciplinary lines; understanding any one of them requires expertise that cuts across several disciplines. For example, oceanic circulation patterns influence and are influenced by atmospheric circulation patterns, rainfall patterns, the topography of the ocean floor, temperature, and the chemistry of water, among other factors. Terrestrial ecosystems are affected by land use, land cover, and the climate system, as well as by the chemistry and biology of their constituent environments; while species within ecosystems are affected by physical-chemical inputs, population genetics, and interactions with other species, including humans. And because so many physical, chemical, and biological processes are strongly affected by and affect human activities, understanding those activities, including the development and use of technology, is integral to the environmental sciences. Thus environmental sciences include branches of social sciences and engineering just as they include branches of biological and physical sciences. For the environmental sciences to build the knowledge base they need, these disparate fields need to cooperate and collaborate.
Making science useful for environmental management is equally complex,
By “multidisciplinary,” the committee means a collaborative approach involving many disciplines; “interdisciplinary” implies integration of multidisciplinary knowledge. This usage conforms to the recent literature (e.g., Hansson 1999, Karlquist 1999, Policansky 1999).
We use the term “natural systems” to refer to systems relatively undisturbed or not controlled by humans, as opposed to agroecosystems or urban areas. We recognize that humans and their activities are an integral part of many biophysical systems on the Earth and that to distinguish between human and natural systems is often a false dichotomy.
requiring a sound scientific and multidisciplinary understanding. Finding effective ways for scientists in a variety of disciplines to work together and to communicate with managers and governments is of great importance both for advancing scientific understanding and for making that understanding useful. It has often been difficult, however, to achieve the needed multidisciplinary collaboration, let alone interdisciplinary integration. The need to do so runs as a theme throughout this report and is implicit in the committee's recommendations. We return to this matter in Chapter 4 .
STUDY PURPOSE AND SCOPE
The National Science Foundation (NSF) supports a wide variety of research in the environmental sciences, and as part of its long-range strategic planning sought advice from the National Research Council (NRC) about the most important and challenging scientific questions in the environmental sciences. NSF expects to use this guidance to help identify new research initiatives and programs that could move basic understanding forward in critical areas.
In response to NSF's request, the NRC established the Committee on Grand Challenges in Environmental Sciences. In recognition of the multidisciplinary nature of the subject under its charge, the committee was also asked to identify factors that may serve as barriers to the implementation of multidisciplinary research agendas, such as educational needs; research infrastructure, including equipment and institutional arrangements; and related matters. The committee consisted of 17 scientists drawn from a broad range of disciplines, including terrestrial and aquatic ecology, paleoecology, biogeochemistry, physical oceanography, biology, chemistry, physics, atmospheric sciences and climatology, hydrology, geology, environmental engineering, medicine, epidemiology, toxicology, geography, political science, economics, and psychology.
The committee's charge was not to identify grand environmental challenges (that is, to list the world's biggest environmental problems). Rather, it was asked to determine the most important research challenges within the environmental sciences, that is, areas of opportunity in which a concerted investment in science could yield new understanding. At the same time, these advances may also be relevant to understanding and solving the world's greatest environmental problems, given that scientific knowledge is a prerequisite for environmental problem solving.
Method of Soliciting Input
In identifying potential grand challenges, the committee made a concerted effort to obtain suggestions from as wide a sampling as possible of the scientific
community and other interested individuals and organizations. The primary tool for soliciting these contributions was a letter inviting the recipients to submit a one-page description of a grand challenge for the committee's consideration (see Appendix A ). This letter, which explained the purpose of the study and the criteria the committee would use to evaluate candidate grand challenges, was distributed to scientists throughout the United States and abroad via the e-mail listservs of dozens of professional scientific societies. Recipients were further invited to pass the invitation on to any others who might want to suggest potential grand challenges. The letter was also sent directly to scientists and managers at major federal government research agencies, to members of the National Academy of Sciences and the National Academy of Engineering, and to many NRC volunteers. An Internet site for the study was established and linked to the sites of scientific societies and other organizations so those who had not been contacted directly could learn about the study and submit their ideas to the committee.
This process for soliciting input generated more than 200 responses from people having a wide variety of backgrounds and affiliations with universities, governments, nongovernmental organizations, and the private sector in the United States and abroad (see Appendix B ). Each submission was read and discussed by the committee. Many of the submitted ideas influenced the committee's deliberations and are reflected in the final list of grand challenges, although none of the submissions is included verbatim.
The committee also considered the results of earlier, similar exercises. These included many reports produced by the NRC, NSF, and others during the last decade that identified important research challenges within various disciplines and involving particular environmental issues.
Process for Selecting Grand Challenges and Immediate Research Investments
In response to the NSF request, the committee attempted to select a short list of high-priority research challenges. This strategy did not involve ranking environmental issues by importance, but evaluating opportunities for maximal research payoff. The committee developed its recommendations in two stages.
The committee first identified important broad areas of research, applying the criteria described below. This exercise resulted in eight grand challenges, along with the highest-priority substantive research areas for each.
The committee then selected four areas to recommend for immediate research investment. These selections resulted from a consideration of all eight grand challenges from the perspective of research implementation. The recommended areas are those the committee judges to have the highest likelihood of yielding a major payoff from increased investment in the next decade, given the current state of relevant science. These are not broad research recommendations addressed primarily to the scientific community, but actions that are intended to
support scientific research and can be implemented by government officials, including NSF staff.
Finally, grand challenges in the environmental sciences may be different from other research activities in that they could require special efforts to develop measurement techniques, databases, or conceptual frameworks; to train scientists in new ways; to establish unusual collaborations among disciplines, universities, and government agencies; and the like. Accordingly, the committee considered these special needs with regard to the scientific enterprises selected as grand challenges.
The committee did not rank-order the grand challenges, nor did it rank-order the research recommendations, for the same reason: each of the challenges selected by the committee meets the above criteria, and each therefore deserves to be pursued vigorously by researchers and supported commensurately by research funders in the United States and worldwide during the next decade and beyond. Consequently, the order in which the challenges and research recommendations appear in subsequent chapters is simply alphabetical.
The committee agreed to select only a small number of grand challenges, even though there are many important and promising areas in the environmental sciences. By agreement with NSF, the committee considered what the most significant research challenges would be during the next 20-30 years. In other words, the committee focused on challenges that are likely to take at least one decade to engage successfully, in part to allow for the training of a critical mass of scientists to undertake the necessary projects. Although the committee did not exclude a priori challenges that could be met in a shorter time, the search favored longer-term scientific efforts.
The committee defined grand challenges substantively, that is, in terms of the kinds of knowledge to be developed. Although there are other sorts of challenges facing the environmental sciences—such as developing new methods and databases, training environmental scientists, and addressing mismatches between scientific needs and the structure of research organizations—we addressed such needs in the context of meeting substantive challenges rather than labeling any of them as grand challenges themselves.
The committee recognized that selecting a few grand challenges from an extensive list would inevitably be a somewhat subjective enterprise. To impose structure on its deliberations, the committee decided to use six criteria for selection:
The challenge must be compelling. We selected only challenges we judged as offering the potential for a large payoff in both scientific and practical
terms. Scientific payoff is of various types, including resolving important unanswered theoretical questions, opening new areas to systematic inquiry and explanation, and finding common explanations for phenomena previously believed to be unrelated. Practical payoff is also of various types, including the generation of useful information for avoiding or mitigating catastrophes, making long-term development plans, making economic choices in the face of environmental changes and uncertainty, and resolving public policy dilemmas.
The challenge must be large, requiring numerous researchers, many years, and appropriate resources. Regardless of how important it might be, a challenge likely to be dealt with satisfactorily in a year or two of diligent, directed effort does not qualify as “grand. ”
The challenge must be relevant to environmental issues of importance to humankind. Challenges were rated more highly if the research would address rapid environmental changes that are likely to require well-informed human responses in the near future, and if the environmental conditions under study would take a long time to correct if research revealed the importance of corrective action.
A fourth criterion was feasibility. The committee favored topics on which research is likely to yield scientific payoff within a decade given the recommended level of effort, or on which an increased research effort now would help build the necessary knowledge base for important results later.
The criterion of timeliness led the committee to emphasize topics on which research would be facilitated by recent developments in technology, data, theory, or scientific collaboration. Our reasoning was that breakthroughs are more likely in fields in which new tools or other capabilities have recently emerged than in those in which the existing research tools have already been in use for a considerable time.
The committee favored challenges that require multidisciplinary collaboration. Challenges that might be met by research within a single discipline or research tradition were not ruled out. However, because multidisciplinary collaboration is both difficult and important for so much of the work in the environmental sciences, as discussed above, major research efforts that would build the capability for multidisciplinary collaboration would have positive spillover effects for the rest of environmental science, and therefore deserve priority.
Immediate Research Investments
To provide a shorter list of more focused recommendations for immediate research support, the committee reexamined the grand challenges and the focused research areas identified for each. We considered a dozen potential action items—research areas that met the above criteria for the grand challenges and could be recommended for immediate research investment. The potential action items outnumbered the grand challenges because the committee considered some
research areas that cut across more than one grand challenge, and because each grand challenge encompassed more than one focused research area.
Choosing among the topics was itself a major challenge. Each topic had substantial merit based on the importance of the scientific questions involved and the potential benefit of increased study. Each could be characterized as timely, important, and even having some urgency. Therefore, the committee revisited its selection criteria and applied additional ones to narrow the list to three or four areas that would be recommended for immediate research investment. For each candidate topic, the committee asked whether the investment in that topic is especially timely, i.e., whether the time is ripe in terms of the balance between what is known and what is likely to be learned. The committee also considered for each topic the level of current research support in relation to the probable need for support. In other words, in identifying topics for immediate research investment, we ranked those we judged to be in need of significant additional funding higher than others, which were often deemed to be of equal intellectual and practical importance. The committee also favored those areas we judged to have potential for major and rapid progress. And we favored research areas for which we believed that significant research funding has the potential to transform disciplines by leading the development of new approaches and by encouraging cross-disciplinary interaction.
ORGANIZATION OF THIS REPORT
Chapter 2 describes the eight grand challenges identified by the committee, while Chapter 3 presents the committee's recommendations for immediate research investments. Chapter 4 addresses implementation issues.