The natural sciences provide an essential knowledge base for wise choices when human activities may have significant environmental consequences. Only through these sciences can decision makers understand the dynamics of environmental systems and the ways in which human actions reverberate through these systems to affect environmental quality. The social and behavioral sciences also provide an essential knowledge base, although their roles are not as commonly recognized or as fully institutionalized in environmental policy. Only through these sciences can decision makers understand which policies will induce the desired human actions in relation to the environment and what ultimate effects environmentally important decisions are likely to have on human well-being. Moreover, environmentally important decisions may themselves be improved with better application of behavioral and social scientific knowledge.
Recognizing the need to develop these kinds of knowledge, the U.S. Environmental Protection Agency (EPA) and the National Science Foundation (NSF) asked the National Academies to identify a few science priorities that could contribute to improved environmental decision making and also advance the social and behavioral sciences. The National Academies were given a broad purview for this study. The study was to consider all relevant social and behavioral scientific perspectives and approaches, both on their own and as they relate to and integrate with perspectives from the natural sciences, engineering, and mathematical sciences. It was to consider research on decision processes in government organizations and elsewhere, as well as research on human-environment relationships that might have practical value for decision making. It was to consider areas of research that
could improve environmentally important decisions regardless of whether the decision makers are government agencies, private companies, other organizations, or individuals. It was to focus, however, on the social and behavioral sciences other than economics because they have not received much attention from decision-making organizations, and to define research areas that would build on strengths in these sciences and link them with each other, with economics, and with the natural sciences so as to produce a deeper understanding of environmental issues. We understood the relevant social and behavioral sciences to include the traditional disciplines of anthropology, geography, political science, psychology, and sociology as well as various associated interdisciplinary fields, such as decision science, communications research, policy sciences, human ecology, and science and technology studies. Thus, we did not consider recommending priority research areas that we judged to fall primarily in economics, regardless of how well those areas might score against the decision criteria we used. This report has two main audiences: potential researchers and potential research sponsors.
The National Academies were asked to recommend research areas that score well as measured against three criteria: the likelihood of achieving significant scientific advances, the potential value of the expected knowledge for improving decisions having important environmental implications, and the likelihood that the research would be used to improve those decisions. They were also asked to consider recommending ways to overcome barriers to the use of research that would have high priority if such barriers could be overcome and invited to make general recommendations for infrastructure that could increase the likelihood that the recommended knowledge across several fields will be used.
HOW WE CONDUCTED THE STUDY
The National Academies organized the study under the auspices of its Committee on the Human Dimensions of Global Change, which has since 1989 advised federal agencies on research issues in the area of human-environment interactions and has produced several previous reports identifying promising research directions (National Research Council, 1992, 1994b, 1999b). The committee participated in selecting the membership of the panel and in reviewing this report. Panel members were selected to include expertise from across the social and behavioral sciences, with strong representation of researchers grounded in these disciplines who are engaged in studying environmental issues. Members also include individuals with backgrounds in the environmental natural sciences and engineering, experience in governmental and private organizations whose decisions have sig-
nificant environmental impact, and expertise in the use of science in policy and organizational decision making.
Identifying Science Priorities
From the outset, we decided to look widely for ideas about research areas that might meet the three decision criteria. Before our first meeting, we sent a message to e-mail lists of all the relevant research groups and networks that we could identify in which we explained the panel’s task, listed our decision criteria, solicited suggestions of research areas from the recipients, and invited them to pass the request along to anyone they thought might have worthy ideas for us to consider.1 We considered all the suggestions that were submitted, along with suggestions from panel members and sponsors at our initial meeting in June 2003, and identified about a dozen broad research fields in which priority areas might lie. We then invited a scientist working in each broad field to write a short memorandum identifying research areas in that field that he or she thought met our decision criteria and to explain this judgment.2 We invited these individuals to discuss their memoranda with us at our second meeting. After that meeting, we invited some of them to expand these into papers that appear as appendices to this report. At our third meeting, we refined our focus to the five recommended research priorities described in Chapters 2 through 6.
Applying the Decision Criteria
The three decision criteria that the panel was given entailed making predictive judgments about the consequences for science and decision making of differential investments in research. Historical examples of important advances in the social and behavioral sciences suggest the difficulty of predicting the path, impacts, costs, and benefits from innovations in the social sciences. If would have been exceedingly difficult, if not impossible, to predict how Garrett Hardin’s famous paper on the “tragedy of the commons” (Hardin, 1968) would have affected researchers in many different fields or stimulated the search for management regimes that do not result in degradation of common property. Although we still do not have definitive answers in this search, much has been learned about what kinds of arrangements tend to work in certain contexts and why they work (e.g., National Research Council, 2002a; Dietz, Ostrom, and Stern, 2003). Certainly the full body of research on problems of managing the commons has had a notable impact, but it would have been very difficult if not impossible to anticipate the nature of the impact or who would use the knowledge. Similarly, it would have been difficult to predict how the development of
the field of applied welfare economics from the 1920s to the 1950s, including the evolution of its many analytic tools in the 1960s and 1970s that together comprise social benefit-cost analysis, would affect environmental decision making today.
These examples suggest that despite the admirable logic of the decision criteria, they are better suited to considering information that is provided for a narrowly defined application than for assessing the potential of basic research or research with a broad range of potential intellectual implications and practical applications. The panel sought nevertheless to discipline the study by repeated reference to the decision criteria, to develop collective judgments in relation to the criteria as conscientiously and consistently as possible, and to seek guidance from past experience and empirical research on the use of knowledge from the social and behavioral sciences in environmental and other practical decision making.
We consulted panel members with expertise in decision processes for advice on what procedure to use to judge potential science priority areas against the criteria. With their advice, we decided that the criteria as given to us were sufficiently vague (and the topics sufficiently unformed) as to make it highly likely that if we used a procedure of voting or subjective weighting of topics against criteria, the results might not be meaningful because different panel members would have interpreted the criteria differently. Consequently, we decided to specify the criteria further by identifying a number of factors that are likely to act as means to the ends outlined in the criteria (described below). Each panel member agreed to consider how each of these contributing factors applied to each research area and to judge that area accordingly against the relevant decision criterion. At the third meeting. we engaged in a discussion of each of the previously identified topics (now accompanied by draft text that ensured a common understanding of what the topic covered) in light of the criteria and the contributing factors in the hope of reaching consensus on which topics deserved inclusion among the science priorities and which, for whatever reasons, did not. The chair held in reserve the option of using a subjective weighting scheme if discussion failed to reach consensus. That option turned out to be unnecessary, as we readily reached consensus. Once it was agreed which topics deserved inclusion, we worked to frame a set of no more than five science priorities that would coherently include the topics that met the criteria. The overall process of selecting topics and applying the decision criteria involved winnowing, combining, and reformulating the topics that had initially been proposed to arrive at the final list.
Likelihood of Achieving Significant Scientific Advances
We rated potential science priorities highly on this criterion when we judged the following factors to be applicable:
The research community is ready and able to conduct the research (e.g., concepts, methods, and data are available but not yet adequately applied in this area).
Successful research would provide new frameworks for thinking or sources of understanding (e.g., data, methods) that could lead to advances in environmental decision making over time.
Successful research would overcome or reduce gaps in knowledge or skill that now inhibit opportunities for improved environmental decisions in a given context.
Potential Value of the Expected Knowledge
We rated potential science priorities highly on this criterion when we judged the following factors to be applicable:
The research findings are relevant for decisions with important environmental consequences and social or economic implications that are significant to affected parties or governments.
The research findings are relevant for a diverse range of environmental decisions.
The research results have significant potential to create, compare, and implement more attractive policy alternatives.
Likelihood That the Research Would Be Used
We informed our judgments of proposed science priorities in relation to this criterion by examining empirical research on the use of scientific findings by various kinds of decision makers. Much of this research focuses on the use of information from the social sciences in government and private-sector organizations (see Appendix A for a review and an annotated bibliography). We also considered the results of research on the factors affecting individuals’ use of information in making environmentally relevant decisions (for reviews, see Gardner and Stern, 2002; National Research Council, 2002b; see also Chapter 5).
The research suggests that the likelihood of use of social science research is affected by attributes of the decision-making organizations, the researchers’ activities, and the links between researchers and users.3 Studies suggest that decision-making organizations are more likely to use science
that they have expressly requested, particularly from internal sources; when unfamiliar problems arise; when there are incentives for seeking information; and when they believe the research can provide authoritative support for their decisions (e.g., Oh, 1996b; Oh and Rich, 1996). Information users’ acquisition efforts are also important in getting research used (Landry, Lamari, and Amara, 2003). The pattern of scientific challenge, in which research results are more likely to be challenged if they threaten well-organized interests, affects the likelihood that scientific findings will be accepted by public policy makers (Freudenburg and Gramling, 2002). Characteristics of the research itself, including technical quality and the extent to which the research directly focuses on user needs rather than on advancing scientific knowledge, are not consistently related to utilization (Landry et al., 2003). However, researchers’ efforts to disseminate results and to adapt their reporting to users’ needs are strongly associated with increased use of the information in some studies (Greenberg and Mandell, 1991; Landry, Amara, and Lamari, 2001; Landry et al., 2003). In addition, research use is facilitated by formal or informal links between researchers and research users (Huberman, 1990; Landry et al., 2001, 2003). Because of the small number of empirical studies on these issues, however, the generality of the findings is uncertain.
We rated potential science priorities highly on the criterion of likely use of research results if we judged the following factors to apply:
Decision makers, such as those in organizations that make environmentally important decisions or among groups affected by such decisions, would be likely to request the research or the information it can yield.
Decision makers, including parties affected by decisions, have incentives to seek and use the information, for example, to help them achieve personal, group, or organizational objectives.
Researchers have incentives to disseminate their findings in ways that usually reach potential users and not only to academic publication outlets.
Good organizational links or intermediaries exist that provide lines of communication or “translation” services between the likely producers and the likely users of the research results.
The above factors favoring the use of research results are not external to the decision-making process. Organizations that support or use research can act to create favorable conditions for using research when those conditions do not already exist. In some of the recommended science priority areas, we have recommended such actions.
The panel recommends five science priorities for improved environmental decision making that, in our judgment, strongly meet the selection criteria we have been given. They are described in detail in Chapters 2 through 6, along with explanations of how the recommended research can improve decision making. We note the priorities briefly here.
Environmental decision processes. We recommend a program of research in the decision sciences addressed to improving the analytical tools and analytic-deliberative processes necessary for good environmental decision making. It would include three components: developing criteria of decision quality; developing and testing formal tools for structuring decision processes; and creating effective processes, often termed analytic-deliberative, in which a broad range of participants take important roles in environmental decisions, including framing and interpreting scientific analyses.
Institutions for environmental governance. We recommend a concerted effort to build scientific understanding needed for designing and evaluating institutions for governing human activities that affect environmental resources. This science priority, which has been identified in several previous National Research Council reports and by the National Science Foundation, would bring together the research traditions of policy analysis and institutional analysis to elaborate science-based tools that participants in environmental decisions can use to improve resource management institutions and to design more effective linkages among institutions at different levels of governance.
Green business decision making. We recommend substantially expanded support for research to understand the influence of environmental considerations in business decisions. The research would address such issues as when and under what conditions better environmental performance provides competitive advantages; how the demands of customers, suppliers, and investors affect environmental performance; how environmental outcomes may be affected by changes in business supply chains; and how environmental accounting procedures and sectoral standard-setting activities can affect environmental outcomes.
Environmentally significant individual behavior. We recommend a concerted research effort to better understand and inform environmentally significant decisions by individuals. This priority includes research in four specific areas: indicators of environmentally significant consumption, fundamental research on consumer choice and constraint, transmission sys-
tems for decision-relevant information for individuals, and integration of information with other policy instruments.
Decision-relevant science for evidence-based environmental policy. We recommend that the federal government strengthen the scientific infrastructure for evidence-based environmental policy by pursuing a research strategy that emphasizes decision relevance. It should do this by developing decision-relevant indicators for environmental policy, including pressures on the environment, environmental states, and human responses and consequences; by making concerted efforts to evaluate environmental policies; by developing better methods for identifying the trends that will determine environmental quality in the future; and by improving methods for determining the distributional impacts of environmental policies and programs. These efforts will require integrating the social sciences and the natural sciences of the environment. Decisions about how to construct indicators, evaluate policies, and so forth will require the involvement of the full range of parties affected by environmental decisions because these choices are not purely technical. Measurement focuses attention on what has been measured, and affected parties often disagree about what is most worth measuring, which outcomes of policies are most important, and the like.
Because we were asked to identify a very small number of science priorities, we have not mentioned many other intriguing and meritorious topics. Here we highlight three topics that, although we have not identified them as separate science priorities, are so pervasive and so linked to several of the science priorities that they warrant attention across the science priority areas.
Innovation and Technological Change
Research on innovation has a long tradition and many different disciplinary sources, including psychology, history, anthropology, political science, economics, geography, and sociology. Many core concepts are shared broadly. For example, the ideas of “first movers” and “late adopters” one encounters in a corporate strategy or management journal have equivalents in each of the other disciplines just noted. Concepts of evolution and adaptation in innovations over time are also widespread, although interdisciplinary awareness of them is not (Erwin and Krakauer, 2004). Early adopters typically pay a premium in economic and other terms compared with those who come later. Innovations may work in some cultures but not in others for any number of empirical, researchable reasons. Issues of communication and education also appear routinely in studies of innovation across
disciplines and fields of human endeavor. Innovation research offers a potentially fruitful approach for understanding and improving environmental decision making.
Innovation is important for environmental policy both because of the role of technological innovation in creating and ameliorating environmental problems and because of the need for policy innovation at all levels and for its diffusion. Issues of innovation are particularly important to our science priorities in the areas of decision-making processes, environmental governance, green business decision making, and individual behavior. Concepts from research on innovation and technological change can usefully be applied in all these priority areas.
Human-environment systems and the policy systems used to govern them are both highly complex. Researchers who study complex systems have developed a variety of concepts that can be useful for understanding these systems and improving their functioning. Consider, for example, the ways the highly capitalized and complex transportation systems upon which modern societies depend may resist the transformations required to sustain these societies into the future. The problem has been termed “technological lock-in” by systems theorists and is reflected in ongoing discussions about the future of a hydrogen-based economy. One can readily build a hydrogen-powered car today, but the technology system required to get the hydrogen to it on a mass market basis does not exist. The gasoline engine is “locked in” by the fuel manufacture and distribution infrastructure. Change is still possible, but it will take much longer, is more complicated, and runs a great risk of generating unanticipated consequences as it ripples through the coupled technological, economic, and social systems (Bijker, Hughes, and Pinch, 1987).
For comparatively less highly capitalized and simpler systems, in which enabling technologies are not tightly coupled, system changes may be easier to come by (Shapiro and Varian, 1999). For example, one can usually change air scrubber technologies without affecting any of the underlying manufacturing technologies, since these are only loosely coupled. This is not the case with a core manufacturing technology such as the use of lead solder in electronics manufacturing, which is tightly coupled to other technologies (Allenby, 1992).
The resilience or brittleness of systems matters too. Resilient systems are capable of absorbing or otherwise dealing with external threats and opportunities. Brittle ones are usually less capable. Proposals to shift to “distributed generation” of energy and electricity arguably underestimate the brittleness of existing and facilitating infrastructures in the face of
change. Brittleness need not preclude innovation, however, as the story of the cell phone and its winning battle with conventional telecommunications indicates so well.
These observations suggest that research that provides environmental decision makers with better understanding of complex systems and their evolution may have widespread value. Organizational studies with a complex systems perspective, especially multisectoral ones exploring the roles and relationships of private, public, not-for-profit, and nongovernmental institutional forms as these relate to environmental innovation and technological change, are likewise attractive. Thus, a complex systems perspective may be usefully applied in the recommended priority areas of improving decision processes, environmental governance, and business decision making.
Combining Social and Natural Science
Even though our task was to identify priorities that flowed out of the social and behavioral sciences, each of our recommended science priorities requires collaboration, and sometimes integration, across the social and natural sciences. Each one builds on measurement and analysis of both biophysical and human conditions and processes, as well as of human-environment interactions. Coupling the social and natural sciences is an increasingly important element of emerging research and development programs in the federal agencies. For example, the NSF’s new cross-directorate program on environmental research and education (ERE) explicitly emphasizes the coupling of human and natural systems and of people and technology (Pfirman and the Advisory Committee for Environmental Research and Education, 2003). It emphasizes as principal research questions “how the environment functions, how people use the environment, how this use changes the environment, … and how the resultant environmental changes affect people” (p. 13). Efforts to implement our recommendations would therefore contribute to efforts at NSF, in federal environmental agencies, and elsewhere to develop the multidisciplinary science needed to inform environmental decisions.
Considering the parallels between this study and forward-looking research planning efforts in federal agencies, it is not surprising to see numerous substantive overlaps in recommendations. For example, the NSF-ERE report identifies numerous recommended research areas, including (Pfirman and the Advisory Committee for Environmental Research and Education, 2003):
Identifying decision processes that effectively combine analytical, deliberative, and participatory approaches to environmental choices, which
will guide scientists and engineers toward the generation of decision-relevant information (p. 35).
Understanding the patterns and driving forces of human consumption of resources, and identifying policies and practices that influence materials and energy use decisions, including incentives (p. 33).
Conceptualizing and assessing the role that institutions play in the use and management of global, national, and local common-pool resources and their associated environmental conditions (p. 36).
Developing decision-making strategies and institutional approaches to most effectively solve problems and deal with uncertainty (p. 35).
Close parallels to each of these recommendations and others from the ERE advisory group can be found in the present study. Our recommendations in turn are completely consistent with the recognition of the NSF-ERE group and others (e.g., National Research Council, 2001a) that an adequate decision-relevant understanding of the environment depends on better coordination across the sciences.
science that examines more broadly the role of science and scientists in a variety of decision and policy processes (e.g., Brunner and Ascher, 1992; Gunderson, Holling, and Light, 1995; Sarewitz, Pielke, and Byerly, 2000; van Asselt, 2000; Freudenburg and Gramling, 2002; Ascher, 2004). Although this tradition contains useful insights regarding how science is used and misused in policy processes, we did not find it useful for judging which research areas are most likely to produce knowledge that will be used.