Motivation of synthesis, with an example on groundwater quality sustainability
 Synthesis of ideas and theories from disparate disciplines is necessary for addressing the major problems faced by society. The best motivation for broad, effective synthesis is the “big idea” that is sufficiently important and inspiring to marshal the appropriate collaborative efforts. Groundwater quality sustainability is posed as an example of one such idea that would potentially unify research efforts in both the sciences and social sciences toward a common, pressing objective.
1. How Does Synthesis Happen?
 Synthesis is the combination of ideas or disciplines to form a theory or system [Jewell and Abate, 2001]. Synthesis across disciplines is difficult, which is why it requires extra effort in the hydrologic sciences among others [National Research Council (NRC), 1991, 2004]. Like any other substantive endeavor, it requires impetus or activation energy. Most importantly, there needs to be motivation for individuals and groups to generate this activation energy. On a small scale of research collaboration (two or three investigators), where most synthesis in science seems to happen, the motivation is relatively simple: the investigators are intensely interested in different facets of a phenomenon and need each other's help to complete the research. This small-scale synthesis certainly results in some important scientific advancements, for example, the discovery of DNA by Watson and Crick; the long collaboration on vadose zone hydrology by Nielsen and Biggar [e.g., Nielsen and Biggar, 1962; Nielsen et al., 1973], but typically does not result in the synthesis of many, disparate disciplines that is often necessary to tackle the toughest problems in science (e.g., predicting impacts of climate change on land and water resources, finding cures for cancer). This paper comments on how this larger scale of synthesis can be motivated and provides a hypothetical example on groundwater quality sustainability.
 One motivation for large-scale synthesis is money: provide the means for researchers to operate under one roof or in a research center, and “they will come.” In our experience, this sometimes works, but only if the group or center is built around a big idea or question that is sufficiently clear, exciting and compelling to unify numerous, disparate disciplines toward a common goal. Thus we assert that the key to synthesis at levels that go beyond the two- or three-investigator scale is recognition and development of the “big idea” or a major goal.
 Some of the best known examples of big idea endeavors that have succeeded include NASA's Apollo Moon Program of 1963–1972 [Cortright, 1975], the Manhattan Project [Smythe, 1945], and the Human Genome Project (http://www.genome.gov/). The driving force behind each of these projects was a well-defined goal that marshaled the efforts and imaginations of large numbers of researchers, planners, designers, builders, etc. Similarly, there exist ongoing efforts to synthesize toward an advanced understanding of how the natural world will respond to climate change. CUAHSI (Consortium of Universities for the Advancement of Hydrologic Sciences, Inc.) is one outgrowth of these efforts, although its mission is broader than the response of hydrologic systems to climate change. We believe there is also a need for a national center for hydrology synthesis that would define unifying themes or project ideas that not only have clear endpoints that keep everyone pulling in approximately the same direction but also will have major impact on the science and on important, societal problems. To jolt various disciplines out of their normal routines and into a more communal realm of synthesis, the theme must be compelling enough to attract a critical mass of workers and it must contain significant, exciting research opportunities. Below we give a hypothetical example of a potentially unifying idea concerning groundwater quality sustainability. First, we will briefly discuss the important rolls of goal-driven and curiosity-driven research.
 Synthesis toward the big idea implies putting all efforts into goal-driven research; i.e., if a research idea does not obviously contribute to the end goal, then it is rejected. To the contrary, we believe it is healthy for some percentage of the research in a center or group to be curiosity driven rather than goal driven. The reason is that, clearly, some of the greatest discoveries were made by accident or by investigators who were simply following their own curiosity rather than a preordained path (e.g., discoveries of penicillin, X-rays, and Teflon). In-depth discussions on serendipity in scientific research and the folly of purely scripted research planning are given by Roberts  and Merton and Barber . In essence, scientific research should not be construed as simply a gun that can be aimed at a target. Some research can function that way, but commonly the path is more circuitous because reaching the “target” requires a chain of discoveries, some of which cannot be anticipated until latter stages of the research. Furthermore, some of these discoveries cannot be anticipated or planned and are basically fallout of curiosity-driven research. One might argue that a synthesis center does not need to include curiosity-driven research, which will happen anyway through the traditional, single-investigator research projects. To the contrary, some percentage of any synthesis effort should be devoted to curiosity-driven research because some of the most productive seeds of curiosity germinate during conversations between those driven mainly by curiosity and those driven more by mission or problem solving. Such conversations are most likely to occur when the appropriate diversity of researchers can interact within a center or collective structure. As Louis Pasteur put it, “Chance favors the prepared mind.”
2. Groundwater Quality Sustainability Problem
 A theme that is sufficiently compelling to bring about real synthesis of disciplines must be both broadly significant and generate a great clarity of purpose among the investigators. In other words, the investigators should largely agree on the end goal and they should feel the importance, or even urgency, of attaining that goal. Naturally, the investigators also need to have intense interest in the research and collaboration that is essential to achieving the goal.
 What themes would fit these criteria today? Examples include the effect of greenhouse gases on climate, response of earth systems to climate change, stem cell research, finding cures for cancer, and so on. At first glance, groundwater quality sustainability hardly seems in the same league as these. Although we think it is in the same league, providing a full justification is beyond the scope of this essay. Using basic observations and inductive reasoning, however, let us use groundwater quality sustainability to exemplify a big idea that cuts across broad segments of science and society.
 Groundwater supplies roughly 40% of drinking water in the United States and greater percentages in rural areas [Alley et al., 1999]. Groundwater resources are vast, comprising about 95 percent of the circulating (i.e., not including glaciers) freshwater on Earth, although only a fraction of these resources are available where they are needed, and a still smaller fraction can be produced without inducing adverse effects (e.g., land subsidence, seawater intrusion). Groundwater moves slowly, with mean groundwater ages typically ranging from decades to centuries to millennia, depending on the groundwater basin and location (x, y, z) within. In most alluvial basin aquifer systems of California and western North America as well as the Gulf Coast, for example, a substantial volume of the groundwater is older than 50 yrs [e.g., Clark and Fritz, 1997; Weissmann et al., 2002; Bethke and Johnson, 2002]. This is particularly significant because most major sources of groundwater contamination in North America were created only within the last 50 yrs. This raises several questions: How will the basin-scale groundwater quality respond to this contamination and how long might the legacy of various contaminant sources last? Is the contaminant transport process that we have set in motion during the last half century merely the early phase of a centuries-long “tracer experiment”? What will be the effects of apparent reductions in contaminant sources due to environmental regulations of the last 25 yrs? Is the quality of much of the groundwater on a decades- or centuries-long, barely detectable, decline?
 Given the basic facts that the age of much or most of the groundwater that we drink is substantially older than the contaminant sources, it is certainly plausible that continuing degradation of groundwater quality may occur. Predicting what will happen, however, is a complex problem. Similarly complex are the societal facets to this issue.
 The purpose of this paper is not to discuss the theoretical underpinnings regarding groundwater quality sustainability and related research. Rather, we will pose the problem as a hypothetical and point out the important components that would both require and motivate synthesis.
2.2. Long-Term Change in Groundwater Quality
 Let us assume it to be plausible that groundwater quality in broad regions of the U.S. may be on a long-term, barely detectable decline. Although research on this issue is limited, there are evidence and analyses concerning groundwater age and age dispersion [Bethke and Johnson, 2002; Weissmann et al., 2002] indicating that this may indeed be happening and that basin-scale dispersion of groundwaters of vastly different ages both moderates the progression of the problem and prolongs, potentially by centuries, the declines in groundwater quality [Fogg et al., 1999; Weissmann et al., 2002; Tompson et al., 1999]. Furthermore, Nativ's  poignant paper on groundwater sustainability convincingly argues that declining groundwater quality due to saltwater intrusion and irrigation with wastewater is seriously threatening the future of water resources in Israel as well as the economic and social fabric that depend on those resources. The Israeli case may offer a preview of the future state of many groundwater basins in the U.S.
 We can further assume that in many groundwater basins, the potentially long time lag between introduction of sources and ultimate effects on deeper groundwater would require at least decades of monitoring data to detect statistically meaningful trends. There are some monitoring data that show long-term degradation of groundwater quality, for example, a four-decade trend of increasing mean nitrate concentration in groundwater of the San Joaquin Valley, California [Dubrovsky et al., 1998]. Furthermore, the NAWQA (National Water Quality Assessment) program of the U.S.G.S. is designed specifically for detection of trends (see special issue on Assessing the Quality of the Nation's Water Resources in Water Resources Impact, 4(4), 37 pp., for an excellent summary of NAWQA). NAWQA, however, has completed only 15 years of monitoring, which would be insufficient to detect any long-term trends on the appropriate timescale in all but the shallowest, most rapidly circulating groundwater systems. Reliable, long-term (multidecadal) data on groundwater quality is rare. Imagine trying to detect global warming with just 10 years of data!
 At a big picture level, another troubling trend concerns the potential effects of groundwater development on groundwater quality. Groundwater overdraft is a widespread problem in many parts of the world. When a system is overdrafted, water levels typically decline substantially because groundwater pumping from wells exceeds the rate of replenishment of the aquifer from surface recharge as well as from adjacent basins. In such basins, most of the groundwater no longer exits to rivers, wetlands, the ocean or other groundwater systems. Rather, it predominantly exits by wells. If the pumped well water is not discharged from the basin by some means, the potential exists for a salt imbalance that can only lead to water quality degradation [e.g., Nativ, 2004]. This is particularly troubling in irrigated agricultural basins (e.g., Salinas and Central Valleys, California) where much of the pumped groundwater is evapotranspired by crops, resulting in a concentration of salts in water leaching past the root zone, and back to the water table. It seems undeniable that such a scenario can only lead to salinization of the groundwater basin. The main, unanswered, largely uninvestigated questions are: “How long would it take, and how can it be avoided?”
2.3. Analogy With Climate Change Research
 The above-discussed timing and groundwater age issues suggest that groundwater quality in many basins may be nonsustainable. This type of problem has important similarities to the greenhouse gas problem. The worst-case consequences of these two phenomena are massive: virtually irreversible climate change versus virtually irreversible groundwater quality degradation. Predictive simulation of the consequences can easily exceed the limits of modeling hardware, software and data availability: global climate modeling versus basin-scale, high-resolution modeling of groundwater quality evolution in the presence of complex heterogeneity. Detection or monitoring of the consequences is problematic because the changes in temperature (in the case of climate change) and groundwater quality occur very slowly relative to a human lifetime. Correction or reversal of the problem would require changes in lifestyle and business practices of broad segments of society, yet visible consequences of such actions might not appear for a long time, probably longer than a human lifetime. This, in turn, presents enormous political and institutional hurdles for dealing with the problem.
 An important difference between the groundwater quality problem and climate change is that major, multidisciplinary research efforts have been directed at the latter, but much less so in the case of the former. We are not saying that much excellent groundwater contamination research does not occur, rather, that this research is neither motivated by, nor sufficiently illuminating of, the long-term groundwater quality sustainability issue. Most groundwater research is directed at local phenomena ranging from the pore scale to the plume scale (e.g., <1 km), whereas the sustainability issue needs a complementary, regional (groundwater basin) approach akin to the global climate models in concept. Granted, many regional groundwater flow models have been built and calibrated primarily for managing groundwater quantity, but these models lack the representation of transport and fate processes that must be included, even for hypothetical long-term analysis of groundwater quality.
 Another difference between the groundwater quality problem and climate change is that the period of record of atmospheric temperature is much longer than the period of record on groundwater quality. It would seem that the groundwater quality problem presents a ripe opportunity for CUAHSI and a hydrologic sciences synthesis center.
3. Social Considerations
 We find that most laypersons as well as groundwater scientists and engineers have been significantly influenced by the fact that most of our groundwater is still relatively uncontaminated. That is, groundwater basins contain vast quantities of water. Most of this water is sufficiently isolated from surface contaminant sources to not become seriously polluted on the timescales over which the sources have been active. Thus our generation as well as the preceding generations have become accustomed to drilling wells into major aquifer systems and extracting water whose quality has essentially been unaffected by anthropogenic activities. This helps obstruct our perception of the phenomenon: “My grandparents had mostly clean groundwater; most (much?) of the groundwater is clean today; naturally, this will hold true in the future.” This lack of perception in the face of a slowly progressing problem has happened repeatedly in human history, and is aptly captured in two concepts referred to as “creeping normalcy” and “landscape amnesia” [Diamond, 2004]. Diamond  provides detailed, sobering accounts on the collapse of past civilizations due partly to mismanagement of natural resources, lack of awareness of long-term consequences, and poor decision making. Creeping normalcy refers to gradual trends that may be difficult to separate from noise. Landscape amnesia refers to landscape degradation that has gone essentially undetected because the timescale of the change is on the order of a human lifespan or more. Because groundwater quality also can be expected to often change very slowly relative to the average human lifespan, one can substitute “groundwater quality” for “landscape.” The typically slow change in groundwater quality together with the lack of historical groundwater quality data make creeping normalcy and groundwater quality amnesia particularly pertinent to the social aspect of the problem.
 Would large-scale destruction of groundwater quality cause the collapse of civilizations? Perhaps not for those societies, including governments and private well owners, rich enough to pay for constantly treating the water for consumption by humans, agriculture and industry, although the economic toll would be formidable even for them. Could the U.S. economy sustain such an additional overhead for water treatment? The question has not been asked, and the studies have not been done. For less affluent societies and individuals, the consequences could indeed be dire, possibly leading to economic and human health crises. Similarly, for ecosystems that depend on groundwater discharge and for agriculture there would appear to be no technological fixes. The impacts would be particularly problematic in rural areas, which have enjoyed the luxury of tapping relatively clean groundwater resources for drinking water and irrigation throughout the industrial age.
 Can the cost of widespread groundwater quality degradation be computed? Conceivably valuation economics research could devise the quantitative means of weighing the costs of preventing contamination now, as opposed to treating the water later. Such a calculation would have to include effects of water pollution on future human health care costs. Any economic analysis should recognize that clean water is a resource necessary to sustain life and, arguably, access to it is an inalienable right.
4. Regulatory Considerations
 Lack of scientific understanding of groundwater quality change, together with the intertwined socioeconomic phenomena of creeping normalcy and groundwater quality amnesia, could lead to considerable lack of credibility of the environmental regulatory system. Although groundwater quality would surely be in greater peril without regulatory efforts, if the groundwater quality is degrading more or less irreversibly despite our regulatory efforts, this will eventually come to light and potentially lead to a political or public backlash against groundwater quality regulation. On the other hand, perhaps environmental regulation is sufficiently effective to avert the problem. There is no way of knowing which assertion is correct without much more in-depth study of the underlying phenomena, including predictive modeling at largely unprecedented space and timescales and long-term monitoring that is largely absent or in its infancy. The future of groundwater quality regulation will ultimately depend on the underlying scientific foundation.
5. Closing Remarks
5.1. Groundwater Quality Sustainability
 The reader may disagree on whether groundwater quality is really degrading irreversibly on a large scale in many basins, although a look at available evidence [e.g., Dubrovsky et al., 1998; Nativ, 2004] should give one pause. It is indeed possible that dilution and biogeochemical attenuation (reactive transport) substantially mitigate the problem. Clearly though, some contaminants appear to be so persistent and recalcitrant (e.g., nitrate, salinity from irrigation, MTBE) that we cannot rely on these attenuation mechanisms to eliminate the problems. The reader may also argue that the progression of this problem is so slow, perhaps even slower than climate change in some systems, that it is not worth worrying about. One counterargument is that these points are merely possibilities and, regardless of one's best hunches, are not sufficiently understood to rely upon for policy and management decisions that are fundamental to the well-being of society. The necessary research to adequately define the problems and the relevant phenomena are largely nonexistent. In other words, we are unwisely gambling with the future of groundwater quality.
 There is much hard and anecdotal evidence today of increasing groundwater contamination. There are thousands of VOC plumes, many discovered only recently and originating from land use practices circa 1940–1950 [NRC, 1984] (also see special issue on Assessing the Quality of the Nation's Water Resources in Water Resources Impact, 4(4), 37 pp.). In California we note an increase in the incidence of contamination of water supply wells just in the last 10 years, particularly from nitrate [e.g., Helperin et al., 2001]. On a recent trip to England, one of us noted that the nitrate concentrations on two different brands of bottled drinking water was much higher (∼12–15 mg/L as N or NO3, not defined) than what we would consider to be pristine, especially for “pure spring water.” If U.S. spring water purveyors were required to print the water chemistry analyses on the labels, we believe they would not be able to successfully market water with such NO3 levels. Does this mean that, because of a longer time available for anthropogenic impact, that regions such as Europe are already seeing advanced stages of a creeping normalcy regarding groundwater quality? There is no answer to this question yet, but it needs attention. Comparative analysis of some European and North American groundwater basins might be particularly illuminating.
 There seems to be an enormous opportunity for synthesis of ideas and theories directed at the goal of understanding how our past, present, and future land and water management actions will affect the quality of our largest reservoir of readily accessible freshwater groundwater. Examples of some of the needed activities include the following, just to name a few.
 1. Continue and expand groundwater monitoring efforts such as NAWQA.
 2. Perform basin-scale groundwater modeling analysis of changes in groundwater quality on timescales of at least centuries. This would represent a paradigm shift for much of the contaminant hydrogeology research and professional communities, which have tended to focus on the transport and fate of point sources of contaminants at the plume scale. Expanding the scope of groundwater contaminant models to basin scales is somewhat analogous to the expansion of meteorology from local weather forecasting to global climate change modeling. This motivates a myriad of research needs, including topics of computational efficiency, basin-scale mass transfer among different geologic media, characterization methods, diffusion processes, and long-term biogeochemical attenuation. Moreover, the basin-scale research would enhance predictions made at the plume scale.
 3. Although mentioned in point 2, biogeochemical attenuation is so important to the long-term behavior of groundwater contaminants that a renewed effort into this area or research at regional space scales and long timescales would be needed. The role of different reactive transport processes in the disparate media present in aquifer-aquitard complexes that are inevitably encountered by regionally migrating contaminants is critical.
 4. Develop new resource management methods and practices to decrease sources of contamination as well as predictive analysis of the ultimate, long-term consequences of such methods and practices.
 5. Investigate the ultimate economic costs to society of various groundwater quality change scenarios. This might involve application of existing or yet-undeveloped economic theory to the analysis of the benefits or services of various ecosystem functions. Although likely to be controversial, such research would be worthwhile. If major regulatory reform is needed, the economic approach may be an effective way of establishing the basis for such reform in terms readily understood by a society that is increasingly detached from the natural world.
 6. Investigate effectiveness of legal and political institutions for dealing with the creeping normalcy problem of groundwater quality and, for that matter, climate change. This topic would include research into new legal and political mechanisms for averting such problems.
5.2. “Big Idea” Approach
 In summary, there are, no doubt, many ways to motivate and sustain synthesis across disciplines. We believe the most effective approach, as measured both by the number of multiauthored papers and service to society, is one driven by the “big idea.” The idea should be simple enough in concept to provide clarity of purpose to a variety of researchers, and sufficiently attractive intellectually to unify those researchers in a truly collaborative venture. This strategy capitalizes on human nature by developing excitement among the researchers that tends to self-sustain both the necessary collaborations and momentum toward the end goal. Money is also an essential ingredient, but will not, by itself, produce the most meaningful results.
 Without a great deal of searching, we were able to put forth one example of what we believe to be a quite viable “big idea” for the hydrologic sciences. We believe that several more such ideas could be developed and would aptly form the core of a hydrologic sciences synthesis center.
 We are grateful for review comments by Kenneth Belitz and an anonymous reviewer that helped improve the clarity and content of the manuscript significantly. We could not have gained the perspective and insights written herein without years of research funding, particularly from the National Science Foundation, the U.S. Department of Agriculture, the University of California Agricultural Experiment Station, University of California Water Resources Center, Occidental Chemical Company, the USEPA Center for Ecological Health Research at UC Davis, NIEHS Superfund Grand (ES-04699), University of California Toxic Substances Teaching and Research Program, and Lawrence Livermore National Laboratory. This paper and its contents are solely the responsibility of the authors and do not necessarily represent the official views of any of the above.