1
Wolman Lecture: Hydrologic Science . . . in Landscapes . . .on a Planet . . . in the Future

Thomas Dunne

School of Environmental Science and Management and Department of Geological Sciences

University of California, Santa Barbara

Background

In 1991 the National Research Council's Committee on Opportunities in the Hydrologic Sciences (COHS or the committee) proposed that there exists, or ought to exist, a distinct geoscience referred to as hydrologic science. Hydrologic science would be analogous to atmospheric science, geologic science, or ocean science but different from traditional hydrology, which the committee equated with engineering or applied hydrology. Both the aims and practice of the newly defined science were to be different from traditional hydrology. The goal of this paper is to examine whether this fledgling science has taken flight; whether it really has become distinct; and, if so, what it needs to sustain flight.

The committee adopted and elaborated on an Earth-science-based definition of hydrologic science, originally proposed by Meinzer (1942) and modified by the Ad Hoc Panel on Hydrology (1962):

Hydrology is the science that treats the waters of the Earth, their occurrence, circulation, and distribution, their chemical and physical properties, and their reaction with their environment, including their relation to living things. The domain of hydrology embraces the full life history of water on the Earth.

This definition reflected developments that had been quietly occurring on several continents since the International Geophysical Year (1957–1958) and that presaged the International Hydrological Decade (1965–1974) and the continuing International Hydrological Program sponsored by United National Educational,



The National Academies | 500 Fifth St. N.W. | Washington, D.C. 20001
Copyright © National Academy of Sciences. All rights reserved.
Terms of Use and Privacy Statement



Below are the first 10 and last 10 pages of uncorrected machine-read text (when available) of this chapter, followed by the top 30 algorithmically extracted key phrases from the chapter as a whole.
Intended to provide our own search engines and external engines with highly rich, chapter-representative searchable text on the opening pages of each chapter. Because it is UNCORRECTED material, please consider the following text as a useful but insufficient proxy for the authoritative book pages.

Do not use for reproduction, copying, pasting, or reading; exclusively for search engines.

OCR for page 10
--> 1 Wolman Lecture: Hydrologic Science . . . in Landscapes . . .on a Planet . . . in the Future Thomas Dunne School of Environmental Science and Management and Department of Geological Sciences University of California, Santa Barbara Background In 1991 the National Research Council's Committee on Opportunities in the Hydrologic Sciences (COHS or the committee) proposed that there exists, or ought to exist, a distinct geoscience referred to as hydrologic science. Hydrologic science would be analogous to atmospheric science, geologic science, or ocean science but different from traditional hydrology, which the committee equated with engineering or applied hydrology. Both the aims and practice of the newly defined science were to be different from traditional hydrology. The goal of this paper is to examine whether this fledgling science has taken flight; whether it really has become distinct; and, if so, what it needs to sustain flight. The committee adopted and elaborated on an Earth-science-based definition of hydrologic science, originally proposed by Meinzer (1942) and modified by the Ad Hoc Panel on Hydrology (1962): Hydrology is the science that treats the waters of the Earth, their occurrence, circulation, and distribution, their chemical and physical properties, and their reaction with their environment, including their relation to living things. The domain of hydrology embraces the full life history of water on the Earth. This definition reflected developments that had been quietly occurring on several continents since the International Geophysical Year (1957–1958) and that presaged the International Hydrological Decade (1965–1974) and the continuing International Hydrological Program sponsored by United National Educational,

OCR for page 10
--> Scientific and Cultural Organization (UNESCO). These programs emphasized the study of hydrologic processes at all scales, the role of water in global-scale environmental processes, the need for regional-scale hydrologic analyses, the importance of hydrochemical processes, and the role of humans and other creatures in the hydrologic cycle. Because geophysicists and geographers were instrumental in developing these programs, and because of the breadth of those two fields as practiced in Europe, the research was seen as relevant to social concerns. It often assimilated hydrological research by engineers and foresters but was free from the pressure of immediate problem solving and design. However, these activities were not widely recognized by most hydrologists and were not strongly coordinated and taught as a coherent science. The committee concluded that, although fundamentally an interdisciplinary activity, hydrologic science, being concerned with continental processes and their participation in the global water balance, should be viewed as a distinct geoscience interacting on a wide range of spatial and temporal scales with the oceanic, atmospheric, and solid-Earth sciences. Exploring these interactions is fundamental to understanding the behavior of water and the materials that it transports. Two points concerning the coherence of this scientific activity were left unresolved by the committee's suggestions: (1) a large number of scientists who study hydrology participate mainly through groups and funding agencies concerned with hydrometeorology and view themselves primarily as atmospheric scientists, and (2) there is still some question about whether hydrogeologists will integrate their activities within the vision of the distinct hydrologic science proposed by the committee or find it more attractive to act mainly within forums of geology and geophysics (Back, 1991). Applied Hydrology or Applicable Hydrologic Science? After reviewing the history of hydrologic applications, the committee argued for the existence and continued support of a hydrologic science distinct from traditional engineering hydrology. This is a point that needs to be carefully stated. The original distinction was not made to deny the value of problem solving or to judge the relative intellectual status of various activities. In fact, the COHS report was replete with promises of contributions to many societal concerns if hydrologic science were to be supported: " . . . the strengthened scientific base of hydrology will contribute directly to improved management of water and environment" (NRC, 1991). The report held out the promise of solutions to specific problems such as "the possible redistribution of water resources due to climate change, the ecological consequences of large-scale water transfers, widespread mining of fossil ground water, the effect of land use changes on the regional hydrologic cycle, the effect of nonpoint sources of pollution on the quality of surface and ground water at a regional scale, and the possibility of

OCR for page 10
--> changing regimes of regional floods and droughts'' (NRC, 1991). The committee argued, however, that historically this prospect had been too immediate: "elaboration of the field, education of its practitioners, and creation of its research culture have . . . been driven by . . . engineering hydrology" (NRC, 1991). Klemes (1988) has also been adamant that scientific research in hydrology be kept distinct from the technological activity of using hydrology to manage water resources. The committee recommended instead the study of hydrologic processes and patterns at a variety of scales. Such pursuits would be free from the pressure to generate simulation models with a weak conceptual base, represented by boxes and arrows in flow diagrams, or with parameter values that have been obtained in a cavalier fashion for immediate application in design or regulation. The committee's hope was a long-term strategy, promising that "basic science" would pay off. Since 1991, however, much has changed in the national perspective about what research should be funded. Although basic environmental science seems to have fared quite well despite dire warnings, there is concern on various sides of hydrologic science that the growing call for applications will unduly constrain the kind of research that is supported. The distinction between traditional applied hydrology and the applicable hydrologic science promoted by the committee represents two subtly different presentations of hydrologic understanding. Engineering courses and texts, which gave most of us our introduction to hydrology, tend to present the subject to users (decision makers, designers, students) as being complete or at least sufficient for action. This tends to focus attention on what is known or at least agreed upon, such as the hydraulics of simple channels or the physics of flow through homogeneous soils. It is natural in such an activity that one tends to search for the simplest definition of a problem to be solved or a task to be accomplished. A typical engineering hydrology task would be to predict flow depth, velocity, and overbank discharge for the design of a river-dredging project that will not cause undue harm to water quality or riparian wetlands (the latter being a relatively modern concern). This approach, focusing on one or a few aspects of the environment and adjusting to them or bringing them under control, has spectacularly advanced human health and welfare. Unfortunately, during the impressive history of this problem solving, society has sometimes changed its mind about what the problem to be solved is and has come to expect more sophisticated, higherdimensional solutions to its needs and desires. For example, the simplification or destruction of aquatic and riparian ecosystems that accompanied many engineering activities formerly admired by society is now generally thought to be undesirable and in need of reversal (as long as the projects retain their capacity to support our material needs, of course!). Also, at least a few of the opinion-making elements of society have realized there are some limits to the stress that environmental systems can sustain and still remain in a preferred state. Meeting these

OCR for page 10
--> expectations often requires a broader analysis of the systems and their influences than was the case earlier. Engineering hydrology also tries to put into the hands of regulators, developers, and their designers the tools (equations, mathematical models, computer codes) that allow objective and quantitative decision making. Raising the confidence of the user, rather than emphasizing uncertainties and digging for deeper forms of knowledge about mechanisms, understandably takes precedence in the mind of the creator or compiler, especially in cases where there is an economic incentive to provide the standard method. Over the past three decades, there have been attempts to make some of these tools more rigorous and mathematical but not necessarily more physically realistic. Alternatively, other hydrologists have tried to make analytical tools more realistic representations of environmental processes by incorporating spatial and mechanistic aspects. After an optimistic beginning, these trends have recently been characterized as uncritical and even misleading. A number of senior engineers have, perhaps unfairly, laid responsibility for both the trend toward elaborate mathematical analysis devoid of mechanism and the optimistic attempts at spatially distributed simulation modeling solely at the door of engineers (Klemes, 1982, 1986; Nash et al., 1990). In fact, responsibility for unwise over-extensions could be laid at many feet. Nevertheless, it is said repeatedly by experienced practitioners (Beven, 1987; Beven et al., 1988; Loague, 1990; Grayson et al., 1992) that uncertainties in physically based simulation modeling are large and, when applied to design, planning, regulation, and other decision making, tend to mislead the consumers of such modeling results. Beven (1987) has even stated that spatially distributed, physically based hydrologic modeling is ripe for some kind of intellectual crisis and revolution that would redefine its scope and realistic possibilities. Similar comments on the misleading aspects of probability analyses, largely resulting from incorrect understanding on the part of users, have been made by Klemes (1982, 1989) and Baker (1993). There is need for a broader discussion of the goals of hydrologic modeling and of the relationship between model construction and empirical investigation than one currently finds in engineering hydrology alone. The alternative presentation of hydrologic understanding, offered by COHS, is that of a science that confronts and even gains energy from its own uncertainties. In other words, it constantly focuses attention on what is not known and emphasizes the need for empirical exploration and explicit attempts to falsify or validate ideas. Such an activity seeks fundamental knowledge of natural processes, beyond the level required to solve a specific problem in construction, environmental management, or regulation. Freed from immediate problem solving and able to continually assess its own progress, the activity aims to construct and improve a coherent body of general theory. It also profits from lateral perspectives into ancillary sciences, looking for combinations of knowledge or analogous approaches. Thus, it is more likely to define questions about the operation of hydrologic systems in broad multidimensional terms. Activity of

OCR for page 10
--> this kind has a good track record of discovering phenomena and insights that can be used to anticipate or solve problems in unexpected ways. The theme of this paper, then, is that there is value in fostering a distinct hydrological science but that it will remain vital only if it discovers new phenomena, processes, or relationships governing the behavior of water and its constituents; it focuses on real hydrologic phenomena, such as floods, droughts, drainage basins, material storages and fluxes, and even large-scale engineering effects such as streamflow modification, soil conservation, or channel modifications; and it communicates itself well, both internally to develop cohesion and record progress and externally to develop support. We should concern ourselves with phenomena that are of some interest to society, even if society must be continually informed about the significance of our research targets. The challenge at present lies in defining ways in which hydrologic scientists might gain support for their activities through functioning as engaged members of society. It is neither wise or even satisfying for hydrologists to develop a welfare mentality in which we expect that our research should be supported simply because we exist. We also need to avoid the delusion of what Petroski (1997) has called the ''linear" model of research and development in which it is assumed that basic research is the only precursor to intelligent problem solving. He recounts many examples of practical solutions to engineering needs preceding and even provoking fundamental understanding. The large-scale support for unfettered, curiosity-driven research promised by Bush (1945) seems in hindsight to have been largely a myth, popularized mainly by scientists who have enjoyed considerable freedom under an umbrella of funding provided subtly by some national concern for military, economic, health, or environmental security. Perhaps a more useful model for a scientist's career would be to see oneself as operating in a "web" of information arising both from nature and from society's interests. Keeping oneself broadly informed about nature, and about social concerns and needs related to the environment, can stimulate ideas and feedback and provide opportunities for gaining support, testing ideas, and contributing to human welfare. Thus, the desire for "freedom" from the pressures of immediate problem solving needs to be tempered with an acknowledgment of the value of stimuli that arise from the practical needs of society. This is true even when those needs are as diffuse as the needs of economists and policy makers to understand the limits of our ability to predict the consequences of large-scale changes in climate or land cover. The following anecdote provides an encouraging example of how a pragmatic concern with water engineering has yielded fundamental hydrologic science of the caliber that any scientist would honor. In the 1950s the water supply engineer Law (1956) pointed out that Britain's post-World War I strategic need to establish a

OCR for page 10
--> timber supply by planting conifers on the uplands of northern Britain would conflict with water supply to the rapidly modernizing industrial cities of England because increased canopy interception and evaporation would reduce the yield of runoff into reservoirs. The initial response from foresters was negative. But Law's (1957) field measurements strengthened his argument, which was taken seriously enough by government resource managers and hydrologists to gain their support for one of the most successful long-term paired-catchment experiments documenting land cover effects on water yield (Calder and Newson, 1979). The experiments were illuminated by studies of the physics of plant-water interactions (Rutter, 1967; Calder, 1990; Shuttleworth, 1989, 1991) that are still in operation. Such experiments have proven useful in analyzing land-atmosphere interactions relevant to both river runoff and global climate processes (Shuttleworth et al., 1984; Shuttleworth, 1988; Gash et al., 1996). The distinction between what is fundamental and enduring and what is immediately useful in hydrology is further shaded by Black's (1995) illumination of the critical importance of "unused" resources. Black points out that, although an individual needs a relatively small amount of water to survive physiologically, much larger amounts are needed per capita to survive as a community and that all of Earth's water is needed to buffer the conditions that allow us to survive as a species. Understanding the state and functioning of water at any of these scales and the relationships between the various scales can be a useful contribution to society, if findings are translated into a form that is accessible to other members of that society. Engineering hydrology was not developed to analyze large-scale processes with multiple feedbacks between various loops in the water cycle. The current large effort led by the U.S. government to explore global sustainability surely ought to include a greater component of hydrologic science, even though it goes unrepresented on the Committee on Global Change Research of the National Research Council (1995). Upon review this distinction between engineering hydrology, with its emphasis on immediate applicability, and a more measured but still pragmatic hydrologic science may seem artificial and unnecessary. However, it has a powerful influence on how hydrology is taught and practiced. Although it is not impossible to combine both aspects in a career, a graduate education program, or a government agency, there are important differences of emphasis. Most participants will become involved in one activity or the other, rarely crossing the boundary between approaches. There is even considerable suspicion across the cultural divide. Consequently, it is important to emphasize that a distinctive contribution to society can be made by harnessing the power of science in the analysis of hydrologic processes in ways that are not usually brought to bear in most engineering applications.

OCR for page 10
--> Impetus for Hydrologic Science The impetus for conducting a distinctive hydrologic science is the persistence of important gaps in society's knowledge about the roles of water in the operation of the Earth at all scales from global to soil profile. These roles are so multifaceted and complex that they cannot be elucidated by the narrowly focused approaches traditionally used in hydrology and taught in hydrology courses and texts, which have emphasized rather uncritical "can-do" approaches to the analysis and solution of water control and environmental problems. Although I have argued above that scientists should never forget their responsibilities, I remain supportive of the original COHS recommendation that there is reason to foster a unified discipline of hydrologic science, distinct from immediate design and regulatory needs. The distinctive requirements of such a science are that it seeks to identify and study fundamental processes, sometimes going beyond the needs of the immediate task or the community interest of the moment; it explores connections to collateral influences on the behavior of water, such as the role of biota, the solid Earth, or the oceans; it aims to construct a coherent body of transferable theory; and it is obligatorily self-critical, taking seriously the importance of falsification through critical measurements. There is great value in fostering such activity, both because it is the interesting and distinctive option in hydrology at this time (Klemes, 1986; Beven, 1987; Dooge, 1988) and because such an activity can contribute to understanding problems of keen societal interest and utility, now and in the future. This opportunity can be illustrated with two examples, both drawn mainly from surface hydrology, that is close to my own experience. Although equally interesting contributions are being made in hydrometeorology, hydrogeology, and biogeochemistry, it is easier to make this point with familiar examples. I argue later that, although the promise of making useful contributions to knowledge exists, the continued vitality of the fledgling hydrologic science is not assured, and it needs some attention from those who place value on it. The two examples derive from assertions that may seem whimsical at first glance. A student will find no more than a passing reference to them in even modern hydrology texts. Yet they are two of the most important realizations in hydrology in the past two decades. The assertions are as follows We live on a planet, and that fact has hydrologic significance ranging from the mechanisms by which the energy and water balances of the entire Earth are stabilized in a range that is hospitable for humans and other biota to investment decisions that must be made by local water authorities about their future water supplies. Furthermore, we now realize that human activities can influence

OCR for page 10
--> the hydrologic cycle on this scale by altering the chemistry and radiative properties of the atmosphere and possibly by transforming the Earth's land cover on a sufficiently large scale. There is considerable interest in anticipating, or at least defining, the uncertainty about the impact of global change on the hydrologic cycle and water resources. We live in landscapes, the topography of which is a dominant influence on spatial and temporal patterns of water storage and surface and subsurface transport of water and its constituents. We also recognize that humans can influence the hydrologic cycle on the scale of even the continental-scale river basins. This is a consequence of the spatial extent of land cover changes and the degree to which humans have intensified or perturbed biogeochemical cycles through pollution and extensive land transformation. Both of these insights present enormous challenges to hydrologic science and simultaneously provide it with opportunities for contributing to human welfare and reducing ecosystem disruption. They do, however, require us to change, or at least expand, our hydrologic science. Significance of Planetary-Scale Hydrology Asrar and Dozier (1994, p. 6) describe the Earth system as "two subsystems—physical climate and biogeochemical cycles—linked by the global hydrologic cycle." Few traditional hydrologists would have thought of elevating the significance of the hydrologic cycle to this level. However, the implied challenge is a measure of the degree to which hydrology has recently been called on, even entrained, by atmospheric scientists to answer questions about the linkage between land surface processes and the atmosphere. Hydrometeorologists seek collaborations to understand the land-atmosphere interactions that influence tropospheric circulation on all scales, particularly the global and regional redistribution of water and heat. Shuttleworth (1988) and Sellers et al. (1997) summarize recent developments and outstanding questions in this field. In order for them to improve their models of land-atmosphere interaction, hydrometeorologists need to refine their knowledge of spatial and temporal patterns of moisture storage and availability for evaporation. Therefore, they need to know about the distributions of soils, plants, and topography and their roles in holding moisture or releasing it to deep ground water or streamflow. Typical wavelengths and amplitudes of topography in various physiographic regions, as well as regional patterns of soil and plant distributions, affect the rate at which water drains from a landscape and therefore the amount and pattern of its storage and availability for evaporation. Although there have been many illustrations of spatially distributed hydrologic modeling, most of them have been concerned with outlining model structures and demonstrating that they can be

OCR for page 10
--> calibrated to match streamflow responses. There has been little use of thoroughly substantiated models to explore the effect of first-order geographical patterns in a way that has some theoretical relevance and widespread applicability, even if only in an approximate way at this time. Eagleson's (1978) papers indicate the combination of rigor and intellectual reach that is needed as a starting point in this field. Blöschl and Sivapalan (1995) and other contributors to the same volume review the hydrologic significance of spatial patterns of soil and topography, and Wood (1995) illustrates how a combination of modeling and remote sensing could yield information about the effect of measurement resolution on computed results. An important challenge for improving our knowledge of hydrology at these continental scales is to better represent processes, material properties, and boundary conditions that are characterized by such small-scale spatial and temporal variations that they cannot be resolved with foreseeable measurement and computational resources. Such processes and properties have to be represented in models through the strategy of parameterization, which expresses the averaged behavior of these unresolvable effects and their multifarious nonlinear interactions on process rates (e.g., the average rate of evaporation, average rate of erosion, or average speed of water evacuation from a landscape). These effects are often presented as a nuisance that hinders prediction because of "parameter uncertainty." Viewed from another perspective, however, they present a focus for investigating characteristic patterns of material properties, of topography, and of the processes themselves, leading to hydrologic discoveries. There is much new science to be done in investigating these patterns and in discovering new aspects of the behavior of water and the materials it carries, rather than focusing most of the discipline's attention on improving computational methods and on calibration of simulation models. Learning how to represent these patterns of materials and processes offers the prospect of improving their model formulation in ways that will truly enhance our understanding of the hydrologic cycle. Encouraging possibilities exist for new forms of hydrologic measurement, taking advantage of the revolutions in electronics and particularly remote sensing. However, these advances are not panaceas. Satellite-based remote sensing yields a pixel-averaged view of the Earth's surface from the top of the atmosphere, with varying degrees of spatial resolution depending on the sensor. In general, remote sensing is better at providing spatial coverage than the temporal coverage valued by small-scale hydrology. We must strive to combine remote sensing products with more thorough and creative fieldwork in order to investigate what is being represented. It is difficult to imagine the range of opportunities offered by satellite-based remote sensing because of the rapid evolution of this technology (Asrar and Dozier, 1994). Much work remains to be done both in interpreting and using remote sensing products for hydrology and in articulating the specific data types and resolutions needed to solve critical hydrologic problems. That work is gradually developing into field campaigns for coordinated

OCR for page 10
--> measurement and, more slowly, into the development of a theory-based consensus about what spatial and temporal patterns of properties and processes need to be investigated. The other side of this emergent interest in planetary and continental-scale hydrology is the need to interpret the hydrologic consequences of any anticipated combinations of climate change and other large-scale environmental change, such as population growth and deforestation. Society needs an improved capacity for predicting the status of water resources (sensu lato) on seasonal-to-interannual time scales that immediately influence human activities. In addition, the results of global and regional models of change (atmospheric general circulation models [GCMs], demographic projections, land use scenarios) need to be translated into predictions of ground-level conditions and processes such as soil-moisture regimes, ground water recharge, runoff volumes, floods, droughts, lake levels, and soil erosion patterns. This effort has begun (Wigley and Jones, 1985; Wolock and Hornberger, 1991; Marengo et al., 1994) but is stymied mainly by uncertainties in GCM-predicted magnitudes or even signs of changes in annual and seasonal precipitation and radiation loads and the need to interpret precipitation event and plant characteristics to be expected under altered climatic regimes. Uncertainties about terrestrial factors can be partially overcome by cautious space-for-time substitutions that introduce reasonable scenarios of expected changes, even if they cannot yet be predicted from first principles. Such scenarios are more likely to be accurate if generated by experienced field scientists with a theoretical turn of mind. The problem of anticipating global warming effects may be a little easier for river basins in the snow zone. Lettenmaier and Gan (1990) and Nash and Gleick (1991) have used a simple model of snowmelt and the resulting basin runoff to analyze the sensitivity of snowpack and soil moisture storage and of seasonal and flood flows to various climate scenarios generated by two GCMs for hypothetical enhanced atmospheric carbon dioxide conditions. The results suggest that significant changes should be expected in the seasonal timing of runoff—that is, more runoff in autumn and winter because of lower ratios of snow to total precipitation and lower spring-summer runoff because of lower snowpack storage. Such changes would have expensive consequences for the kind and amount of artificial streamflow regulation that might one day be needed. However, much better spatial and temporal resolution is required in both the atmospheric and land surface models before much confidence can be placed in anything other than the sign of the results. The easily available models, originally developed for calculating the water balance of individual soil profiles or for quasi-black box forecasting of floods, are simply too crude to rely on the quantitative results. However, the results are convincing enough to give some urgency to the task of improving modeling capability for large river basins. They may also compel society to seriously consider the possibility of major disruptions of its water storage, supply system, and flood risk in the snow zone. In addition to model developments,

OCR for page 10
--> uncertainty must be reduced concerning representative field conditions in basins typical of the physiographic region. These include the amount of ground water storage, the interannual carryover of water, and the influence of elevation effects on snowpack accumulation and the energy balance. A combination of field surveys and remote sensing of the current range of conditions will be needed to allow model-based extrapolations into unsampled environments. This can best be accomplished with coordinated empirical and modeling studies. Throughout such an effort, however, hydrologists must be responsible for explaining to people the significance of even preliminary results and why such an investment in measurement is required to gradually reduce uncertainty. By comparison with the climatological and meteorological uncertainties, differences of emphasis among hydrologists about modern process-based models and the difficulties of parameterizing them seem small. Beven et al. (1988), Wood et al. (1988), and Robinson et al. (1995) among others have drawn together the current level of field experience into a convincing theory of how hillslope and channel network characteristics govern basin hydrologic response, including the distribution of soil moisture at a range of geographical scales. This statement is not meant to ignore the massive problems introduced by both systemic and parameter uncertainty in process-based modeling of surface hydrology (Beven and Binley, 1992; Grayson et al., 1992; Beven, 1993; Jakeman and Hornberger, 1993). However, some of those problems arise from a lack of attention to uncertainties that can be reduced with field measurement or from asking intractably difficult questions in the first place. The optimal recursive blend of computation and field measurement is rarely explored in answering broad, socially relevant questions in hydrology. This situation needs to be changed, possibly through strategies suggested at the end of this paper. Appreciation that planetary-scale atmospheric changes might affect continental climate and hydrology has also resulted in the resurgence of empirical hydroclimatology. Redmond and Koch (1991) have investigated the statistical association between indices of large-scale atmospheric circulation, seasonal precipitation, air temperature, and regional patterns of streamflow during the past half-century. They showed that winter precipitation (October-March) and annual streamflow are generally low in the Pacific Northwest during El Niño-Southern Oscillation events. These conditions involve a weakening of atmospheric pressure gradients across the Pacific, a weakening of easterly winds along the equator, and higher-than-average sea surface temperatures off South America. Equatorial sea-surface temperatures strongly affect the transport of heat, pressure distribution, and wind patterns in midlatitudes. Values of the pressure anomaly indices known as the Southern Oscillation Index and the Pacific/North America Index during the preceding June-November period correlate with Pacific Northwest rainfall during October-March. Winter air temperature, on the other hand, is negatively correlated with this atmospheric index. Drier-than-average winters thus tend to be warmer than average. This association enhances the variability of snowmelt contributions to streams.

OCR for page 10
--> philosophical principles of science. Mathematics is obviously a requirement because of the need to formalize theories for exact definition, communication, testing, and prediction. It is widely agreed that this is so, and to judge from journal articles, some progress has been made in improving the average analytical skill level of people entering the field of hydrology. However, Dooge, Klemes, and others have warned repeatedly that mathematical training alone is not sufficient to build hydrologic theory. Something more fundamental is required. We need to remind ourselves and our students of the principles and methods of science, including its goal of developing general theories of nature, its search for fundamental mechanisms, and its empirical tools both for exploration and hypothesis testing. Lack of numeracy is declining as a communications block in the geosciences. Even many students who are esthetically attracted to traditionally descriptive field sciences are quite willing to study advanced mathematics, continuum mechanics, chemical kinetics, and other useful hydrologic tools given sufficient reason to do so. These are not the students who studied mathematics early in their careers because they were certain that it would be good for them. They still need convincing and motivating by concrete scientific applications before they will extend their mathematical skills. Helping students acquire these skills should be a goal of modern graduate education in hydrologic science. Hydrologic science is also recruiting students with strong analytical skills but little experience with landscapes, planets, processes, or measurement. It is difficult to expect students with no exposure to basic climatology, physical geography, or ecology to generate the idea of studying, say, the processes that lead to rainfall distributions over topography and their role in flood generation or how climatic changes might gradually affect plant community characteristics and hence the water balance. Thus, we also need to create some time in the education of these scientists to learn about the physics, chemistry, and biology of waters near the Earth's surface. New kinds of introductory graduate-level courses that present a quantitative and theoretical approach to some of these fields would probably attract both kinds of students described above and help them to recognize the overarching geoscience themes that proponents of hydrologic science have outlined. At present, we do not communicate well enough to build hydrologic science into a broad, rapidly growing, socially useful activity. That problem can only be solved by behavioral changes forced by professors, hiring committees, employers, and editors. The crucial action eventually, however, will have to be curriculum reform. In a few universities that have the flexibility and funds to invest in new, sufficiently large Ph.D. programs in hydrologic science, it will be easier to hire and acculturate a diverse faculty covering the range of subjects referred to in the COHS report, provided that the leadership is open minded on this subject. At other universities a program in hydrologic science will have to be coordinated from offerings already in various departments of engineering, Earth science, atmospheric science, forestry, and related disciplines. The strains that Klemes

OCR for page 10
--> (1986) has described between hydrologic research and technological applications of hydrology in resource management are likely to be difficult to manage under such circumstances, unless the Earth or atmospheric science departments are stronger, larger, and more committed to studies of land surface processes than is usually the case. In the case of departmental or interdepartmental graduate programs in hydrologic science, both National Aeronautics Space Administration (NASA) Earth System Science fellowships and especially the original National Science Foundation (NSF) fellowships in hydrologic science (five per institution for five years) have been a crucial form of support that allows graduate students to pursue an interdisciplinary course between faculty advisers without having to devote a large amount of time to assisting the research of the faculty member. Improving Measurement Capabilities Measurement and even qualitative observation have always been weak components in the training of hydrologists. Most hydrology books never mention the characteristics of real land surfaces or describe processes occurring on them over a range of time scales. It is tacitly acknowledged that, because of the scale problem referred to in earlier sections, it is difficult to visually identify any characteristic or process being represented in a hydrologic model. Data, supplied from networks of rain gages or stream gages by the technical staffs of federal agencies, are usually taken at face value, their limitations given only passing mention. Most hydrology textbooks have early sections on how to fill gaps in data series and generally "make do" with whatever fragmentary data happen to be available in the project area of interest. This passivity has left most of us unskilled in conceiving of innovative and precise measurement techniques. Exceptions to this generalization are the skillful measurements of small-scale subsurface water storage and flow processes in some field and laboratory experiments and monitoring studies. Yet there have recently been some technological revolutions affecting the availability, or in some cases the promise, of more and better data than have been available before. Despite recent retrenchments in some federal government stream-gaging programs, during the last decade of this century we are probably receiving more hydrologically relevant data than have been collected in the entire history of the science, and the pace of measurement shows no sign of slowing. Digital topography of the United States and most of the Earth's continents at spatial resolutions of 30 or 90 m is already, or soon will be, available, and higher-resolution data will emerge, as side-looking airborne radar is deployed from satellites and aircraft. Laser altimeters on aircraft already produce high-resolution topography for special purposes. Distributions of atmospheric water vapor are mapped with passive microwave sensors on spacecraft, and higher-resolution spatial and temporal distributions of individual rainstorms are measured with ground-level radar (Smith et al., 1996a, b). Global satellite measurements of

OCR for page 10
--> radiation and surface temperature are available for monthly averages, with the promise of much higher resolution following the launch of satellites under the Earth Observing System and other programs by NASA and National Oceanic and Atmospheric Administration (NOAA) (Asrar and Dozier, 1994). Other data bases include regular measurements of snow distribution and the condition of plant covers, as well as low-frequency compilations of ground-level or satellite measurements of plant distributions, land cover, and soil properties. In the wings are promises of optical monitoring of snow cover (Rosenthal and Dozier, 1996), radar measurements of snow water equivalent (Shi and Dozier, 1996), high-precision topography for low-lying areas such as valley floors, and even surface soil moisture for some restricted range of environments. The entry of NASA and NOAA into the field of hydrology has thus been a revolutionary force, facilitating analyses that were simply impossible earlier. In the United States, although there has been some reduction in the number of monitoring stations, even traditional measurements of rainfall, streamflow, water chemistry, and soil properties are more easily available than ever because of a vast effort by some federal agencies to disseminate data through electronic media. These data sources are not without blemish, of course. The resolution of routinely available digital topography is still too coarse to reflect the scale of the dynamics of runoff and erosion; radar rainfall is difficult to calibrate and interpret; measurements of plant conditions are compromised by atmospheric aerosols and other effects; and the litany of difficulties goes on. Many uncertainties remain in interpreting the ground-level radiation signal received at the top of the atmosphere. However, all of the examples represent major improvements in useful hydrologic data, especially in terms of spatial coverage. They are simply too promising and pervasive to be ignored in the training and retraining of hydrologic scientists. A significant time commitment to remote sensing and spatial data handling is now required in hydrologic training, including time spent critically reviewing the relationship between the interpreted product and actual ground conditions (which themselves may be difficult to define). Remotely sensed products allow us to observe large remote features such as entire continents, river basins, mountain ranges, and floodplains. Thus, they are crucial to our ability to observe large-scale processes such as floodplain inundation (Sippel et al., 1994; Vorosmarty et al., 1996; Mertes, 1997), rainfall fields (Smith, 1996b), and the generation of massive sediment pulses from regional-scale intense rainfall. They also contribute to the goal of constructing credible spatially distributed runoff and evaporation models. Most of the new data sources referred to above are being delivered to hydrology without being ordered. In the traditional manner of "making do" with data from networks installed for purposes associated with water management, surface water hydrologists are muddling through, grateful for every new bit of data we can get our hands on. In particular, the satellite-based sensors were developed for other reasons and have been turned to purposes useful to us mainly by geophysi-

OCR for page 10
--> cists, atmospheric scientists, and others. Some of these groups are now in a position to recommend satellite and other remote sensing programs to provide critical measurements for their scientific purposes. However, among hydrologic scientists, only hydrometeorologists seem in a position to make such requests, because of the previously mentioned lack of theoretical convergence and agenda building among hydrologists. The chance to guide hydrologic data collection could be an important product of agenda building. A particular example of directed data collection that was highlighted by COHS was the opportunity to participate in large, coordinated, multiinvestigator field campaigns, such as the First ISLSCP (International Satellite Land Surface Climatology Program) Field Experiment (FIFE), Hydrologic-Atmospheric Pilot Experiments (HAPEX) and Boreal Ecosystem-Atmosphere Study (BOREAS), and the upcoming Large-Scale Biosphere-Atmosphere in Amazonia (LBA) (Amazon Basin) and GEWEX (Global Energy and Water Cycle Experiment) Continental-Scale International Project (GCIP) (mainly Mississippi River basin) activities. So far, it is the hydrometeorologists who have been able to take advantage of these opportunities, and surface water hydrologists continue to lag behind in the effectiveness of their data requests. Oversight Though referred to above as a fledgling, hydrologic science is important to transcendent societal concerns such as the reciprocal interaction between humans and climate, global sustainability, environmental justice between nations and generations, and the influence of continental perturbations on the nearshore ("green-water") ocean. For this reason the science needs to be fostered as a strategic concern—perhaps as the special concern of some standing oversight body, analogous to the Climate Research Committee of the National Research Council (NRC), a committee overseen by the Board on Atmospheric Sciences and Climate. The most appropriate venue for such a Water Science Committee could be the NRC's Water Science and Technology Board (WSTB). The WSTB already works for hydrologic science, including its sponsorship of the original Committee on Opportunities in the Hydrologic Sciences and in fact has been the only such voice in this country in recent decades. However, most of the board's work is ultimately related to the technological issues that reflect the interests of the federal agencies that support the WSTB. Creating a Water Science Committee to nurture and develop hydrologic science would provide for a separation of emphases similar to that being proposed among hydrologists themselves. It would be desirable for such a committee to continue fostering hydrologic science, more or less as described in the original COHS report but with more direct acknowledgment of the ethical responsibilities of environmental scientists to work on problems of broad social concern. The standing committee would be composed of a small, broadly informed group of hydrologists with a range of

OCR for page 10
--> backgrounds who take seriously the responsibility for hydrologic science as a whole, rather than representing, say geomorphology, ground water hydrology, or hydrometeorology. They would have to see themselves as trustees, representing the interests of the next generation of hydrologists and all the nonhydrologists who pay the bills of the science. The committee members could articulate trends or gaps in knowledge, thereby providing continuous advice to the directors of funding programs and building consensus about research strategies for the science. The committee could sponsor regional seminars and special sessions at professional meetings. It could publish occasional commentaries. Dissemination of information about the contributions of hydrologic science to human knowledge and its plans for extending that knowledge would be another important activity. Several other sciences, most notably astronomy, have proven that frequent representation on the weekly science pages of the New York Times, combined with a strong community research agenda skillfully communicated to Congress, seem to be associated with the ability to mobilize massive investment in that research agenda. On the water planet, hydrologic science should be at least as diverting as the stars. In its oversight of the science the committee could take some responsibility for maximizing the nation's entire investment in hydrologic research by promoting interactions between academe and the federal agencies interested in water. This interaction has declined precipitously during the past 10 to 15 years as federal budgets have tightened. However, communication depends on attitudes, even in the absence of money. A decline in optimism has also reduced the probability of new research collaborations and the transmission of ideas. During times of slow hiring, federal agencies become isolated from the stream of bright young people who continue to pass through universities. Academics lose contact with valued colleagues, underutilized data sources and equipment, and interesting scientific problems motivated by the agencies' responsibilities. This running down of the federal-academe relationship is a loss to the nation, and it needs to be reversed at little or no cost. Exchanging information and sharing joint responsibility for a national scientific committee with an optimistic charge could initiate this reversal. Visits and expressions of interest in each other's programs (research and nonresearch) would be easy steps in reestablishing a fruitful relationship. Concerning how to fund such an activity, a straw proposal is presented to provoke thought among those who look wearily on any proposal for new activity at this time. A small and active (publishing several essay-length reports per year) standing NRC committee might cost $150,000 per year. Six annual contributions of $25,000 would suffice. These contributions could be sought among a variety of institutions that stand to gain from direct representation on the committee or from a continuous stream of ideas about opportunities for research that might be useful to its operation. The directors of the NSF and NASA hydrology programs might find that such information would reduce their need for outside advice from

OCR for page 10
--> current sources, so that they might be able to divert some of the resources they currently use for that purpose. Some federal agencies with a need to keep informed about developments in scientific hydrology might also be induced to contribute. Since secondary goals of the committee would be to advertise widely the contributions of scientific hydrology and to stimulate agency-academe productivity, there are reasons for the committee to be useful to several agencies. Finally, the national organizations that represent private interests in water and power might also be induced to provide stable annual funding for a committee with a long-range strategic view of the science. Summary This author does not share the Sputnik-era confidence of some colleagues that hydrologic science left to its own devices would automatically improve human welfare. However, a modestly supervised hydrologic science, imbued with strong philosophical and ethical principles about the conduct of scientific research on behalf of society, could be of enormous benefit to the nation and to its collateral field of applied hydrology. Much good hydrologic science can already be found in the premier journals of hydrology, but it is spread so thinly amid excellent representations of other types of work that the ethos of hydrologic science does not emerge. As Klemes (1988) has pointed out, the science and the nonscience in hydrology frequently become mixed up, to the confusion of both. Before a strong hydrologic science can grow and interact productively with the other geosciences, some actions and permanent behavioral changes are needed. We need to develop more unified approaches in our choice of important research targets and in our quest for theoretical generalizations about fundamental processes. We must put aside differences of background and have the patience to communicate with each other so that everyone understands the current state of knowledge, or at least knows exactly why he or she disagrees with it. We have to extend our ability to use or at least to understand a wide variety of new technologies that for the first time offer to measure the spatial characteristics of hydrologic processes and characteristics at scales up to regional and global. Finally, the oversight mentioned above needs to be provided by the NRC, which would not only act as an authoritative voice on scientific hydrology but also generate a stream of creative advice about continuing opportunities in hydrologic science. Acknowledgments I am very grateful to Steve Burges and Jeff Dozier, who in many conversations helped to clarify some of the issues raised here, and to Bill Dietrich and Laura Ehlers for reviewing the manuscript.

OCR for page 10
--> References Abraham, A. D., and J. J. Ponczynski. 1976. Drainage density in relation to precipitation intensity in the U.S.A. J. Hydrol. 75:383–388. Ad Hoc Panel on Hydrology. 1962. Scientific Hydrology. U.S. Federal Council for Science and Technology. Washington, D.C. Ahnert, F. 1976. Brief description of a comprehensive three-dimensional process-response model of landform development. Z. Geomorphol. 25(Suppl.):29–49. Asrar, G., and J. Dozier. 1994. Science Strategy for the Earth Observing System. Woodbury, N.Y.: American Institute of Physics Press. Back, W. 1991. Opportunities in the hydrological sciences. EOS Am. Geophys. Union Trans. 72:491–492. Baker, V. R. 1993. Flood hazards-learning from the past. Nature 361(6411):402–403. Benda, L. E., and T. Dunne. 1998a. Stochastic forcing of sediment supply to channel networks by landsliding and debris flow. Water Resour. Res. 33:2849–2863. Benda, L. E., and T. Dunne. 1998b. Stochastic forcing of sediment transport in channel networks. Water Resour. Res. 33:2865–2880. Benda, L. E., D. J. Miller, T. Dunne, G. H. Reeves, and J. K. Agee. In press. Dynamic landscape systems. In Ecology and Management of Streams and Rivers in the Pacific Northwest Coastal Ecoregion. R. J. Naiman and R. E. Bilby, eds. New York: Springer-Verlag. Beven, K. J. 1986. Hillslope runoff processes and flood frequency characteristics. Pp. 187–202 in Hillslope Processes. A. D. Abrahams, ed. St. Leonards, Australia: Allen & Unwin. Beven, K. 1987. Towards a new paradigm in hydrology. In Proc. Symp. On Water for the Future Wallingtonford, U.K.: International Association of Hydrological Sciences. Beven, K. 1989. Changing ideas in hydrology—the case of physically-based models. J. Hydrol. 105:157–172. Beven, K. J. 1993. Prophecy, reality, and uncertainty in distributed hydrologic modeling. Adv. Water Resour. 16:41–51. Beven, K. 1996. Equifinality and uncertainty in geomorphological modeling. Pp. 289–313 in The Scientific Nature of Geomorphology. B. L. Rhoads and C. E. Thorn, eds. New York: John Wiley & Sons. Beven, K. J., and A. M. Binley. 1992. The future of distributed models: Model calibration and uncertainty prediction. Hydrol, Process. 6:279–298. Beven, K., and M. Kirkby. 1979. A physically-based variable contributing area model of basin hydrology. Hydrol. Sci. Bull. 24:43–69. Beven, K. J., E. F. Wood, and M. Sivapalan. 1988. On hydrological heterogeneity—Catchment morphology and catchment response. J. Hydrol. 100:353–375. Black, P. E. 1995. The critical role of ''unused'' resources. Water Resour. Bull. 31:589–592. Blöschl, G., and M. Sivapalan. 1995. Scale issues in hydrologic modeling: A review. Hydrol. Process. 9:251–290. Bush, V. 1945. Science—The Endless Frontier. Washington, D.C.: National Research Council. Calder, I. R. 1990. Evaporation in the Uplands. Chichester, U.K.: Wiley. Calder, I. R., and M. D. Newson. 1979. Land-use and upland water resources in Britain—a strategic look. Water Resour. Bull. 15:1628–1639. Cayan, D. R., and D. H. Peterson. 1990. The influence of North Pacific circulation on streamflow in the west. Pp. 375–398 in Aspects of Climate Variability in the Pacific and Western Americas. D. H. Peterson, ed. Washington, D.C.: American Geophysical Union. Chagnon, S. A. 1985. Research agenda for floods to solve a policy failure. Am. Soc. Civ. Eng. J. Water Resour. Plan. Manage. 111:54–64. Crozier, M. J., E. E. Vaughan, and J. M. Tippett. 1990. Relative instability of colluvium-filled bedrock depressions. Earth Surf. Process. Landforms 15(4):329–339.

OCR for page 10
--> Dietrich, W. E., and T. Dunne. 1978. Sediment budget for a small catchment in mountainous terrain. Z. Geomorphol. 29(Suppl.):191–206. Dietrich, W. E., and T. Dunne. 1993. The channel head. Pp. 175–220 in Channel Networks: A Geomorphological Perspective. K. J. Beven and M. J. Kirkby, eds. Chichester, U.K.: John Wiley & Sons. Dietrich, W. E., R. Reiss, M-L. Hsu, and D. R. Montgomery. 1995. A process-based model for colluvial soil depth and shallow landsliding using digital elevation data. Hydrol. Process. 9:383–400. Dooge, J. C. 1986. Looking for hydrologic laws. Water Resour. Res. 22:46S–58S. Dooge, J. C. 1988. Hydrology in perspective. Hydrol. Sci. J. 33:61–85. Duffy, C. J. 1988. Groundwater circulation in a closed desert basin: Topographic scaling and climatic forcing. Water Resour. Res. 24:1675–1688. Dunne, T. 1980. Formation and controls of channel networks. Prog. Phys. Geog. 4:213–239. Dunne, T., T. R. Moore, and C. H. Taylor. 1975. Recognition and prediction of runoff producing zones in humid areas. Hydrol. Sci. Bull. 20:305–327. Dunne, T., L. A. K. Mertes, R. H. Meade, J. E. Richey, and B. R. Forsberg. 1998 Exchanges of sediment between the floodplain and channel of the Amazon River in Brazil. Geol. Soc. Am. Bull. 110:450–467. Eagleson, P. S. 1978. Climate, soil, and vegetation. Water Resour. Res. 15:705–776. Gash, J. H. C., C. A. Nobre, J. M. Roberts, and R. L. Victoria (eds.). 1996. Amazonian Deforestation and Climate. Chichester, U.K.: John Wiley & Sons. Gell-Mann, M. 1994. The Quark and the Jaguar: Adventures in the Simple and the Complex. New York: W. H. Freeman. Gomez, B., L. A. K. Mertes, J. D. Phillips, F. J. Magilligan, and L. A. James. 1995. Sediment Characteristics of an Extreme Flood: 1993 Upper Mississippi River Valley. Geology 23:963–966. Graf, W. L. 1994. Plutonium in the Rio Grande: Environmental Change and Contamination in the Nuclear Age. New York: Oxford University Press. Grayson, R. B., I. D. Moore, and T. A. McMahon. 1992. Physically based hydrologic modeling. 2. Is the concept realistic? Water Resour. Res. 28:2659–2666. Gupta, V. K., E. Waymire, and C. T. Wang. 1980. A representation of an instantaneous unit hydrograph from geomorphology. Water Resour. Res. 16:855–862. Horton, R. E. 1945. Erosional development of streams and their drainage basins: Hydrophysical approach to quantitative morphology. Geol. Soc. Am. Bull. 56:275–370. Jakeman, A. J., and G. M. Hornberger. 1993. How much complexity is warranted in a rainfall-runoff model? Water Resour. Res. 29:2637–2649. Jones, J. A., and G. E. Grant. 1996. Peak flow responses to clear-cutting and roads in small and large basins, western Cascades, Oregon. Water Resour. Res. 32:959–974. Junk, W., P. B. Bayley, and R. E. Sparks. 1989. The flood-pulse concept in river-floodplain systems. Pp. 110–127 in Proceedings of the Large River Symposium. D. P. Doge, ed. Ottawa: Canadian Department of Fisheries and Oceans. Kesel, R. H., E. G. Yodis, and D. J. McCraw. 1992. An approximation of the sediment budget of the lower Mississippi River prior to major human modification. Earth Surface Process. Landforms 17:711–722. Kirkby, M. J. 1986. A two-dimensional simulation model for slope and stream evolution. Pp. 203–222 in Hillslope Processes. A. D. Abrahams, ed. St. Leonards, Australia: Allen and Unwin. Kirkby, M. J., and R. J. Chorley. 1967. Throughflow, overland flow and erosion, Bull. Int. Assoc. Sci. Hydrol. 12:5–21. Klemes, V. 1982. Empirical and causal models in hydrology. Pp. 95–104 in Scientific Basis of Water Resource Management. Washington, D.C.: National Academy Press.

OCR for page 10
--> Klemes, V. 1986. Dilettantism in hydrology: Transition or destiny? Water Resour. Res. 22: 177S–188S. Klemes, V. 1988. A hydrological perspective. J. Hydrol. 100: 3–28. Klemes, V. 1989. The improbable probabilities of extreme floods and droughts. Pp. 43–51 in Hydrology and Disasters. O. Starosolszky and O. M. Melder, eds, London: James and James. Law, F. 1956. The effect of afforestation on the yield of water catchment areas. J. Br. Waterwks. Assoc. 38: 489–494. Law, F. 1957. Measurement of rainfall, interception, and evaporation losses in a plantation of Sitka spruce trees. Int. Assoc. Hydrol. Sci. 44: 397–411. Lewin, J., B. E. Davies, and P. J. Wolfenden. 1977. Interactions between channel change and historic mining sediments. Pp. 353–368 in River Channel Changes. K. J. Gregory, ed. Chichester, U.K.: John Wiley. Lettenmaier, D. P., and T. Y. Gan. 1990. Hydrologic sensitivities of the Sacramento-San Joaquin River basin, California, to global warming. Water Resour. Res. 26: 69–86. Loague, K. 1990. R-5 revisited 2. Reevaluation of a quasi-physically based rainfall-runoff model with supplemental information. Water Resour, Res. 26: 973–987. Maidment, D. R. (ed.). 1993. Handbook of Hydrology. New York: McGraw-Hill. Marengo, J. A., J. R. Miller, G. L. Russell, C. E. Rosenzweig, and F. Abramopoulos. 1994. Calculations of river-runoff in the GISS GCM: Impact of a new land-surface parameterization and runoff routing model on the hydrology of the River. Clim. Dynam. 10: 349–361. Marron, D. C. 1992. Floodplain storage of mine tailings in the Belle Fourche river system: A sediment budget approach. Earth Sur. Process. Landforms 17: 675–685. Meade, R. H. (ed.). 1995. Contaminants in the Mississippi River, 1987–92. U.S. Geol. Surv. Circ. 1133. Denver, Colorado, U.S. Geological Survey. Meade, R. H., T. R. Yuzyk, and T. J. Day. 1990. Movement and storage of sediment in rivers of the United States and Canada. Pp. 255–280 in The Geology of North America, O–1: Surface Water Hydrology. M. G. Wolman and H. C. Riggs, eds. Boulder: Geological Society of America. Meinzer, O. E. 1942. Hydrology. New York: Dover Publications. Mertes, L. A. K. 1997. Description and significance of the perirheic zone on inundated floodplains. Water Resour. Res. 33: 1749–1762. Mertes, L. A. K., T. Dunne, and L. A. Martinelli. 1996. Channel-floodplain geomorphology along the Solimoes-Amazon River, Brazil. Geol. Soc. Am. Bull. 108:1089–1107. Meyboom, P. 1962. Patterns of groundwater flow in the prairie profile. Pp. 5–20 in Proc. Hydrology Symposium No. 3. Ottawa, Ontario: National Research Council of Canada. Miller, N. L., and J. Kim. 1996. Numerical prediction of precipitation and river flow over the Russian River watershed during the January 1995 California storms. Bull. Am. Meteorol. Soc. 77: 101–105. Moore, I. D., P. E. Gessler, G. A. Nielsen, and G. A. Peterson. 1993. Soil attribute prediction using terrain analysis. Soil Sci. Soc. Am. J. 57:443–452. Myers, M. F., and G. F. White. 1993. The challenge of the Mississippi flood, Environment 35: 6–35. Nash, L. L., and P. H. Gleick. 1991. Sensitivity of streamflow in the Colorado basin to climatic changes. J. Hydrol. 125:221–241. Nash, J. E., P. S. Eagleson, J. R. Philip, and W. H. Van der Molen. 1990. The education of hydrologists. Hydrol. Sci. J. 35: 597–607. National Academy of Sciences. 1997. Advisor, Teacher, Role Model, Friend: On Being a Mentor to Students in Science and Engineering . Washington, D.C.: National Academy Press. National Research Council. 1991. Opportunities in the Hydrologic Sciences. Washington, D.C.: National Academy Press. National Research Council. 1995. A Review of the U.S. Global Change Research Program and NASA's Mission to Planet Earth/Earth Observing System. Washington, D.C.: National Academy Press.

OCR for page 10
--> Nicholas, A. P., and D. E. Walling. 1997. Modeling Flood Hydraulics and Overbank Deposition on River Floodplains. Earth Sur. Process. and Landforms 22(N1):59–77. Petroski, H. 1997. Development and Research. Am. Sci. 85: 210–213. Potter, P. E. 1978. The significance and origin of big rivers. J. Geol. 86: 13–33. Power, M. E., A. Sun, G. Parker, W. E. Dietrich, and J. T. Wooton. 1995. Hydraulic food-chain models. BioScience 45: 159–167. Redmond, K. T., and R. W. Koch. 1991. Surface climate and streamflow variability in the western United States and their relationship to large-scale circulation indices. Water Resour, Res. 27: 2381–2399. Robinson, J. S., M. Sivapalan, and J. D. Snell. 1995. On the relative roles of hillslope processes, channel routing, and network geomorphology in the hydrologic response of natural catchments. Water Resour. Res. 31: 3089–3101. Rodríguez-Iturbe, I., and J. B. Valdes. 1979. The geomorphological structure of hydrologic response. Water Resour. Res. 15(6):1435–1444. Rosenthal, W., and J. Dozier. 1996. Automated mapping of montane snow cover at subpixel resolution from the Landsat Thematic Mapper. Water Resour. Res. 32:115–130. Rutter, A. J. 1967. An analysis of evaporation from a stand of Scots pine. Pp. 403–418 in Forest Hydrology. W. E. Sopper and H. W. Lull, eds. Oxford, England: Pergamon Press. Sellers, P. J., R. E. Dickinson, D. A. Randall, A. K. Betts, F. G. Hall, J. A. Berry, G. J. Collatz, A. S. Denning, H. A. Mooney, C. A. Nobre, N. Sato, C. B. Field, and A. Henderson-Sellers. 1997. Modeling the exchanges of energy, water, and carbon between continents and the atmosphere. Science 275: 502–505. Seyfried, M. S., and B. P. Wilcox. 1995. Scale and the nature of spatial variability: Field examples having implications for hydrologic modeling. Water Resour. Res. 31: 173–184. Shi, J., and J. Dozier. 1996. Estimation of snow water equivalence using SIR-C/X-SAR. 1996 IEEE Proceedings from International Geoscience and Remote Sensing Symposium, 96CH35875IV:2002–2004. Piscataway, New Jersey: Institute of Electrical and Electronics Engineers. Shuttleworth, W. J. 1988. Macrohydrology: The new challenge for process hydrology. J. Hydrol. 100: 31–56. Shuttleworth, W. J. 1989. Micrometeorology of temperate and tropical forest. Philos. Trans. R. Soc. London, Ser. B. 324: 299–334. Shuttleworth, W. J. 1991. Evaporation models in hydrology. Pp. 93–120 in Land Surface Evaporation: Measurement and Parameterization. T. J. Schmugge and J-C. André, eds. New York: Springer Verlag. Shuttleworth, W. J., J. H. C. Gash, C. R. Lloyd, C. J. Moore, J. Roberts , A. O. de Marques, G. Fisch, V. P. de Silva, M. N. Ribeiro, L. C. B. Molion, L. D. A. de Sa, J. C. Nobre, O. M. R. Cabral, S. R. Patel, and J. C. Moraes. 1984. Eddy correlation measurements of energy partition for Amazonian forest. Q. J. R. Meteorol. Soc. 110: 1143–1162. Sippel, S. K., S. K. Hamilton, J. M. Melack, and B. Choudhury. 1994. Passive microwave satellite observations of seasonal variations of inundation area in the Amazon River floodplain, Brazil. Remote Sensing Environ. 4:70–76. Smith, J. A., D. J. Seko, M. L. Baeck, and M. D. Hurlow. 1996a. An intercomparison study of NEXRAD precipitation studies. Water Resour. Res. 32:2035–2045. Smith, J. A., M. L. Baeck, M. Steiner, and A. J. Miller. 1996b. Catastrophic rainfall from an upslope thunderstorm in the central Appalachians: The Rapidan storm of June 27, 1995. Water Resour. Res. 32: 3099–3113. Smith, T. R., B. Birnir, and G. E. Merchant. 1998a. Towards an elementary theory of drainage basin evolution: I. The theoretical basis. Compu. and Geosci. 23(9): 811–822. Smith, T. R., G. E. Merchant, and B. Birnir. 1998b. Towards an elementary theory of drainage basin evolution: II. A computational evaluation. Compu. and Geosci. 23(9): 823–849.

OCR for page 10
--> Stanford, J. A., and J. V. Ward. 1993. An ecosystem perspective of alluvial rivers: Connectivity and the hyporheic corridor. J. N. Am. Benthol. Soc. 12:48–60. Stedinger, J. R., and V. R. Baker. 1987. Surface water hydrology: Historical and paleoflood information. Rev. Geophys, 25:119–124. Toth, J. 1963. A theoretical analysis of ground water flow in small drainage basins. J. Geophys. Res. 68:4795–4812. Toth, J. 1966. Mapping and interpretation of field phenomena for groundwater reconnaissance in a Prairie environment, Alberta, Canada. Bull. Int. Assoc. Sci. Hydrol. 11 (2):20–68. Trimble, S. W. 1983. A sediment budget for Coon Creek basin in the driftless area, Wisconsin, 1853–1977. Am. J. Sci. 283:454–474. Vannote, R. L., G. W. Minshall, K. W. Cummins, J. R. Sedell, and C. E. Cushing. 1980. The river continuum concept. Can. J. Fish. Aquat. Sci. 37:130–137. Vorosmarty, C. J., C. J. Willmott, B. J. Choudhury, A. L. Schloss, T. K. Stearns, S. M. Robeson, and T. J. Dorman. 1996. Analyzing the discharge regime of a large tropical river through remote sensing, ground-based climatic data, and modeling. Water Resour. Res. 32:3137–3150. Webb, R. H., and J. L. Betancourt. 1990. Climatic effects on flood frequency: An example from southern Arizona. Pp. 61–66 in Proceedings of the. Sixth Annual Pacific Climate (PACLIM) Workshop. J. L. Betancourt and A. M. Mackay, eds. California Department of Water Resources, Sacramento: Interagency Ecological Studies Program for the Sacramento-San Joaquin Estuary, Technical Rep. 23. Weinberg, A. M. 1972. Science and trans-science. Pp. 105–122 in Civilization and Science: In Conflict or Collaboration? Amsterdam: Elsevier. Whalton, P. H., D. Gilman, and M. A. J. Williams. 1990. Rainfall and river flow variability in Asia, Australia, and East Africa linked to El Niño—Southern Oscillation events. Pp. 71–82 in Lessons for Human Survival: Nature's Record from the Quaternary. P. Bishop, ed. Sydney: Geological Society of Australia. Wigley, T. M. L., and P. D. Jones. 1985. Influence of precipitation changes and direct CO2 effects on streamflow. Nature 314:149–151. Willgoose, G. R., R. L. Bras, and I. Rodriguez-Iturbe. 1991. A physically-based coupled network growth and hillslope evolution model, 1. Theory. Water Resour. Res. 27:1671–1684. Wolock, D. M., and G. M. Hornberger. 1991. Hydrological effects of changes in levels of atmospheric carbon dioxide, J. Forecast. 10: 105–116. Wood, E. F. 1995. Scaling behavior of hydrological fluxes and variables: Empirical studies using a hydrological model and remote sensing data. Hydrol. Process. 10:21–36. Wood, E. F., M. Sivapalan, K. Beven, and L. Band. 1988. Effects of spatial variability and scale with implications to hydrologic modeling. J. Hydrol. 102:29–47. Ziemer, R. R., and J. S. Albright. 1987. Subsurface pipeflow dynamics of north-coastal California swale systems. Pp. 71–90 in Erosion and Sedimentation in the Pacific Rim. R. Beschta, T. Blinn, G. E. Grant, F. J. Swanson and G. G. Ice, eds. Wallingford, United Kingdom: International Association of Hydrological Sciences.