We live in a time when the effects of 150 years of fossil fuel burning may be impacting the environment, and the increase in the human population of the planet is forcing more of humanity onto less productive lands, into parts of the landscape that have never before been occupied in such large numbers. This leaves much of humanity increasingly in harm’s way, on steep hillslopes, on flood plains, and in very arid lands. The study of Earth's surface processes (geomorphology) and of their history that lays the context for the ongoing human experiment (the Quaternary sciences) are and should be at the forefront of research activities dealing with the environment and with hazards.
We describe a major new initiative that directly addresses these issues. Titled Predictive Earth Surface Dynamics, this initiative has two major research activities aimed at different time scales. As a means of promoting collaborative multi-PI research focused on the parallel development of major data sets and comprehensive models, the Whole Basin Dynamics initiative would entail long-term study of a small set of basins, including both the erosional and depositional systems. Water and sediment budgets could be closed, and modern process studies would focus on measurement of the fluxes, the effect on and by biota on these fluxes, and residence times and sources of sediment. Without long-term monitoring of sediment fluxes, it is not possible to close sediment budgets over an effective range of time scales. The time scales under consideration will range up to millions of years, requiring use of Quaternary stratigraphic and dating methods to generate constraints on the sedimentation, denudation and rock uplift patterns. Cooperation between the geomorphology and Quaternary geology communities will propel us towards quantitative integration of modern-process research and the formation of the stratigraphic record. While we do not identify the particular basins in this document, we outline the requisite qualities that selected basins should have. Intensive field study of modern processes over long enough time scales to encompass the variability of the meteorological forcing of the systems will provide strong constraints on physically-based models that account for major physical, chemical and biological processes. Indeed, a key element of this initiative would be development of a community landscape dynamics model. This model would be designed in a modular fashion to allow portability and improvement of units as our knowledge of a process changes.
The linked effort titled Sustainable Landscapes is aimed at developing an integrated set of predictive tools for event-based hazards prediction and mitigation (landscape forecasting), and century-long predictions of surface process responses to global change scenarios (landscape prediction). As in the Whole Basin studies, both field and model efforts are needed. One crucial difference is that in the Sustainable Landscapes initiative, anthropogenically modified landscapes can and should be included. We propose in particular a "2050 project" in which the state of a particular landscape system is predicted under a variety of climate change and landuse scenarios.
For both initiatives, detailed topography is crucial. For the Sustainable Landscapes initiative, topographic data must be gathered and be made available readily, on the scales at which individual landslides occur, and on which the subtleties of flood plains can be read.
We need to foster several research efforts at the join between surface processes and other fields. For example, research at the join with solid earth geophysics, aimed at understanding the geomorphic-tectonic feedbacks in the generation of topography, has proved a tremendous boon to both communities. This encourages continued interaction, we suggest that an active tectonic component be among the criteria for systems to be considered for the Whole-Basin Initiative discussed above. In addition, we suggest that a great opportunity exists on the frontiers: in the study of submarine and planetary surfaces. Not only are these environments intrinsically exciting, but the solutions of landscape evolution problems on these surfaces, on which the values of the fundamental variables differ markedly from those in the terrestrial environment, pose very strong tests of our understanding of these and more familiar terrestrial landscapes.
All of these efforts require infrastructural support above and beyond that now available. Crucial to the quantitative study of surface processes over time scales of more than a few years are high-quality estimates of erosion and deposition rates based on geochemical and other techniques. There is tremendous need for widened accessibility to age determination facilities, both traditional (14C) and newly developed (e.g., cosmogenic radionuclides). These latter techniques have aided tremendously in placing temporal constraints on heretofore undatable surfaces. Also critical is detailed knowledge of surface topography. We propose that a facility be created that will focus on the generation of very high resolution (2m) topography, for which at present the best tool is laser-altimetry. This facility would also be responsible for archiving such data, and for providing an interface between the geomorphic community and the sources of remote imagery that are at present scattered, difficult, and expensive to use. Instrumentation pools akin to those developed in support of other earth science efforts (e.g., UNAVCO, IRIS, PICO) would greatly enhance the quality and uniformity of the science, and potentially reduce the final costs. Experimental facilities at which major process-based research is done must be funded and should be maintained with an open-door policy (e.g., Institute for the Rock Magnetism to the magnetics community) allowing any PI to propose and carry out an experiment.
Finally, we propose new efforts to bring the science to the public. Earth surface processes are familiar to most people, and naturally attract the public to the earth sciences. Effective visualizations can bring the geomorphic processes to colleges, secondary schools, and the general public via numerous science and natural history museums. Geography and geology introductory textbooks, AGI lab manuals, Encyclopedia Britannica, and municipal museums are logical venues for visualizations packaged in a CD. Working with K-12 educators, some of these visualization efforts can be repackaged for elementary, middle, and high school students. In fact, we propose to work toward adoption of an earth science curriculum by high schools. Any serious effort to use broadcast media to take this science to the public should be supported strongly. In addition, the initiatives we have proposed have major implications for civil and environmental engineering. What we learn from the Predictive Earth Surface Dynamics initiative will be shared with working engineers in a series of workshops and short courses offered at professional meetings. Information will then be disseminated to appropriate municipal offices through these channels.
Introduction
scientific rationale and motivation for surface processes and Quaternary research
scientific process
The Plan for 2000
A. New initiatives: Predictive Earth Surface Dynamics
I. Whole Basin Dynamics
II. Sustainable Landscapes
B. Research at the frontiers: submarine and planetary surfaces
C. Infrastructure
• Chronology
• High resolution digital topographic mapping resources
• Shared field equipment program
• National laboratories for Experimental Surface Process Dynamics.
D. Education and Outreach
• Inform public - decision makers, regulatory agencies
• Create pipeline - K-12, college
• Research training - graduate programs
A VISION FOR GEOMORPHOLOGY AND QUATERNARY SCIENCE
BEYOND 2000
Introduction
Scientific Rationale
As is so succinctly stated in the GEO2000 introduction, humans have not only achieved the ability to alter the planet in significant ways, but now stand more squarely than ever before in the path of nature's processes. Humans live on Earth's land surface, not in the interior of the planet, not under the sea. It is the alteration of the planet's surface that most greatly impacts society; it is the frequencies and intensities of the surface processes driven by the weather systems that collectively constitute the climate that affect the human condition. In most places on Earth, the regolith on which our agriculture depends is only a few meters thick, and in some places much less than this. This thin layer of dirt can evolve in place chemically (e.g., be depleted of nutrients), and it is mobile. In order to understand how humankind affects Earth, and vice versa, one must therefore understand the fluxes of sediment in all their multifarious forms. One must understand the movements of that fragile layer of regolith beneath our feet, which nurtures plants, harbors animals, buttresses our foundations, and sometimes buries communities or even civilizations in their tracks.
These facts in turn place geomorphology, the study of Earth's surface and its processes, and the Quaternary sciences, the study of the history of Earth's surface through the last two million years, in the forefront of research on global change. If practiced with rigor, these sciences can act as the link between the solid earth (traditional geology and geophysics) and the climate system; they are the essence and the connective tissue of earth system science.
The AGU has recently (February 2 1999, EOS, v.80, p.49) published its position that humans have most likely altered the planet by causing a component of global change through alteration of the trace gas content of the atmosphere. Yet it is not the changes in the gas that we breathe that threatens the human condition. Rather, humans are affected by the alteration of the hydrologic cycle, the delivery or lack of delivery of storms, the warming of the surface and consequent melting of sea ice and glaciers, the change in the seasonality of precipitation and hence the timing and duration of runoff, the change in intensity (and location) of landfalls of hurricanes. Even more specifically, it is not the rain (or the lack of rain) itself, but often the geomorphic processes that the presence or absence of rain triggers -- landslides, floods, debris flows, deflation, dune migration, wind storms -- that affect humans. The geomorphic response to global change is what most directly impacts humans. It is the challenge of understanding this response that the surface processes community faces: our ability to predict and to mitigate the effects of global change rests on the community’s acceptance of this challenge and the products of the research that this entails.
One of the major foci of study for geomorphology in this next decade and century should therefore be the understanding of the likely impact of global change on the geomorphic system. This should translate into our ability to suggest the likely scenarios for alteration of the geomorphic system, how to monitor this change as it occurs, and suggest how humans occupying the landscape could best deal with this change.
Increasingly, humans live in harm's way. Even in the absence of changes in climate, it has been shown convincingly that portions of the landscape that are subject to large events (floods, waves, droughts) are being occupied more densely. It is this fact that has caused the exponential increase in the costs of disasters through the latter half of the century (Van der Vink et al., Nov. 3, 1998 EOS). That growing populations are forcing humans into portions of landscapes that were previously unoccupied only expands the set of hazards top which humans are subjected, and makes more difficult the strategies for mitigating them.
Quaternary science provides the long term perspective against which perturbations by humans must be viewed. In addition, the Quaternary record reflects numerous completed experiments in global change and its geomorphic consequences. Geomorphic processes do not simply elicit a physical response in the landscape; they leave behind chemical, (fossil) biological, as well as physical records. Changes in Quaternary landscapes have occurred over various time scales; some were long, on the order of glacial to interglacial time scales, while others such as catastrophic floods took place in a matter of hours. Some changes reflect past global changes in climate, while others reflect local or regional phenomena. Whatever the time scale or geographical extent, the record of these past events comprise the modern landscape. Quaternary science investigates what these processes were and seeks to identify their rates. The Quaternary is indeed the bridge between the recent and the deep past. Importantly, it is also the time slice that is most relevant to the understanding of likely outcomes of the ongoing human experiment.
As Quaternarists have long known, the impacts of global change differ from one landscape to the next. Because the intensity and even the sign of global change varies geographically, the geomorphic response to such change differs radically. Some areas, such as high latitude regions and the continental interiors, are more sensitive to climate changes, whether these changes are primarily in temperature, effective moisture, or the seasonality and spatial pattern of precipitation. The options for human response to geomorphic change in the future will vary from place to place, reflecting the population density, the political environment, and the magnitude and style of the change.
The argument for the study of global change are based upon the economic and physical needs of society. The problems of environmental change and of hazard identification and mitigation are problems that impact the pocketbook. However, it would be incorrect, even dishonest, not to admit that some of modern geomorphology is driven instead by curiosity, pure and simple. This acknowledges that another important component of the human condition is the drive to explore, the drive for adventure. These sorts of problems tug at the heart strings rather than the purse strings. The pursuit and the solutions of aesthetically motivated questions satisfy us and in turn fire anew our curiosity about the world and the universe around us.
These sorts of problems include exploration of the origin of patterns in nature. Examples include the origin and maintenance of sorted circles in the Arctic, the ripples and dunes in air and in water, the spacing between channels, the topological pattern of channel networks. These are the patterns one witnesses while traveling through a landscape; they are the coin of landscape photography. We have found that many of these geomorphic systems are self-organizing, and in this sense are as alive as some chemical systems. It was curiosity about such patterns that stimulated exploration of fractal geometries (Mandlebrot was curious about coastline lengths and channel branching networks.)
This class of motivations drives our exploration of new frontiers. While much of the terrestrial sphere has been explored (this is not to say understood), we have much to learn about the underwater world. And we have much to learn about the planets in this and other solar systems. As mechanical and engineering innovations allow us to explore these worlds, largely through remote sensing, we are poised to pose and to answer questions about these other worlds. The tales of planetary evolution are written on the surfaces of these planets, reflected both in their morphologies and their near-surface stratigraphic records. As yet, geomorphologists have not pursued these reserach opportunities extensively. As the number of missions increases and the resolution of the data increases, we need to embrace the challenge of studying these radically different environments. The problems are incredibly rich: life requires water, and water leaves a geomorphic record. The record of how the climate on Mars, for instance, moved from a free water world to a frozen water world will be read largely in the geomorphology. The last gasp of the free-water world will likely have been periglacial in nature.
The scientific process
No matter what the motivation, the study of these systems has at least the following ingredients, all of which must be accomplished with a high degree of quantitative rigor: 1) development of process theory, 2) observation and monitoring of natural systems, 3) modeling of system response in laboratory and numerical experiments, 4) integration and comparison of theory, observation and modeling, and the comparison of these with 5) study of the history of a landscape and the climate to which it has been subjected.
1) We must understand the fundamental physics and chemistry of each relevant process. We cannot predict the hazards associated with lahars before we know something about the physics of lahar flow, rheology, etc. other examples This requires that funding agencies continu to support fundamental research on process, including laboratory, theoretical and field studies designed to elucidate the physics and chemistry involved. Most of the processes are in one way or another non-linear. The most obvious of these effects is the thresholded nature of many processes (e.g. sediment transport, vegetative response to changes in precipitation, lake chemistry response to changes in temperature). To complicate matters, it has been shown through the study of the late Quaternary record that the climate system is non-linear in that it may flip between states very rapidly (decades). It is often as well the case that the process being studied has components that are deterministic and others that are probabilistic, or stochastic. Not only is the forcing of the system (meteorology in most cases, seismic in others) stochastic, but the response at a grain scale, where the forces are being applied must be described as stochastic.
2) Many of these processes, in fact most of them, and particularly the most dangerous ones, are episodic but not necessarily cyclic. The largest events are the rarest, be it wind storms or floods. This statistical reality, arising from the stochastic nature of the meteorological forcing and the non-linearity of the physical processes triggered, requires that we establish and maintain instrumentation that will allow monitoring both the relevant meteorological forcing of the landscape system and the geomorphic response to it. Most ground-level meteorological instrumentation is in lowlands and at airports. Instrumented watershed studies are located in montane regions, but the scales of these watersheds are very small. Indeed, at many levels within the Earth system, scaling remains a serious problem. To make matters worse, many USGS gauges have been decommissioned within the last decade.
Satellite based remote sensing technology has raised the possibility of monitoring over larger scales than ever before, but the problems with temporal and spatial resolution remain obstacles that cannot be ignored. Remote sensing is not a panacea. Each of these new and sophisticated sensors requires ground-truthing. The catastrophic and sudden nature of many geomorphic processes require high frequency monitoring, at rates that are higher than those set by the fixed rate of passage of satellites over an area. The nature of event-based geomorphology is that nothing happens for large periods of time, and then all heck breaks loose. Some events are over before the satellite comes around again. We therefore need ground instrumentation that is 'smart', meaning capable of increasing the sampling rate when something interesting happens. The advent of the miniaturization of sensor and dataloggers and of the decline in price of such instrumentation packages makes it viable to establish such monitoring systems.
3) The earth's surface is geometrically complex and it is dealt a stochastic set of meteorological events. Hillslopes are not planar. Channels are not linear and are in fact networks with variable topology. Models of even an isolated process that assume steady state or that assume simple geometries are therefore incapable of addressing this component of reality. The active processes vary from one place to another in a real landscape, requiring that models or simulations of events or of climate change be capable of simulating the full linkage of processes in a catchment or a system. This cannot be done analytically. It requires numerical models into which are coded the best representations of the physics and chemistry of the relevant processes and that can act on realistically complex terrain. Happily, the exponential increase in computational power over the last couple decades, and the continued development of numerical software has driven a tremendous surge in modeling capability within geomorphology.
4) A better integration of experimental, theoretical, and field studies involving multiple investigators will provide opportunities for increased communication, cross-fertilization of ideas, and dramatic new insights. If the experimental set-ups and carefully chosen field settings are tightly integrated, the field studies are comprised of watershed basins of sufficient size and are continued for a sufficient length of time, and if the field studies are designed intelligently, then data of general applicability will emerge. Such non-site-specific data-sets are essential for understanding the physics and chemistry of the processes.
5) The time scales over which landscapes are altered range from glacial to interglacial time scales to hours to mere seconds. However, any one particular landscape we inhabit is a result of many geomorphic events. In many glaciated landscapes, the last glaciation has erased the record of all previous glaciations, but numerous pothole lakes provide excellent recorders of climate and landscape changes. Sediment lithology, mineralogy, and the assemblage of preserved pollen, diatom, ostracode and other terrestrial and aquatic organisms reveal a rich story of rapid or abrupt (decadal) and gradual (millennial) changes that have occurred during the late Quaternary. Long records from western Europe and northwestern South America have produced a picture of past terrestrial climate that can be compared with Deep Sea records. Desert landscapes are providing a record of lower temporal resolution but that nevertheless contain invaluable information about geomorphic processes that shaped them as well as when these events occurred. More recently, the combination of drought and agricultural practice nearly mobilized the dune fields of the Great Plains regions in the Dust Bowl decades. Integration of shallow marine and terrestrial records are now revealing a record of large amplitude oscillation between high lake and low lake Saharan Africa that varies over the Holocene with millennial periods akin to those recorded in the Greenland ice cores. This variability, the last fluctuation of which was the two-peaked Little Ice Age, is the most recent context for the modern industrial era.
The plan for 2000 and beyond
Given the above rationale for surface process and Quaternary research, we propose several thrusts for new research as we enter the first decade of the next millennium. Each of these activities is described within the body of the report to follow:
• A. A broad new initiative for these sciences called Predictive Earth Surface Dynamics, which has two interactive and substantial research components
• B. Research on the frontiers with submarine and planetary sciences
• C. Supporting infrastructure that will enable and facilitate continued and new process and Quaternary research
• D. Outreach efforts at the K-12 and adult education levels
A. Proposal for an Initiative within the National Science Foundation to be called:
Predictive Earth Surface Dynamics
The focus of this initiative will be a community-level effort to develop and test landscape models for predicting mass fluxes and landform change at time scales ranging from individual storm events to millions of years. Unlike the fields of atmospheric sciences, ocean sciences, hydrologic sciences or solid earth geophysics, no community-wide models exist that can be used to predict and explain landscape erosion, landform change, and deposition of sediment. This gap leaves the community unable to respond to pressing environmental needs, such as landscape restoration, or prediction and mitigation of surficial geologic hazards, illustrated by the recent calamities associated with the landfall of Hurricane Mitch. We stand flat-footed in the face of questions regarding global climate change, unable to provide predictions based on a coherent theoretical framework.
Geomorphology has become much more quantitative in the last 20 years. This has been fueled in part by contributions from engineers, geophysicists and physicists recently drawn to field, by digital topographic (and other) data, by new dating techniques, and by conceptual breakthroughs. Elements of a general theoretical framework and enhanced understanding of landscape processes and form have emerged from this period. We are now well engaged in the research and debate about the fundamental laws governing generation and transportation of debris on the surface, out of which concensus will eventually emerge. This places the community in a position to work on the linkages and feedbacks between these processes. It is unreasonable to expect this to arise from a single individual or a small group because of the vast range of skills, knowledge and data needed to do so. Currently there are many instructive models about landscape evolution, but the vast majority remain unverified, or are too generic to be be useful for short term prediction on real landscapes.
It is now time to bring the burst of discovery and tool development to a collaborative effort directed towards the common enterprise of landscape models of mass fluxes and landscape change. This common enterprise would lead to creation of a small set of General Earth Surface Dynamics Models (GESDM) that can serve to guide theoretical, experimental and field studies. The models would serve both as a fundamental framework for exploration of landscape evolution, and as a practical tool for addressing pressing environmental problems.
This initiative will have two complementary programs: Whole Basin Dynamics and Sustainable Landscapes. In addition, five distinct infrastructure (support) facilities common to and necessary for both programs are suggested:
1) Environmental geochronology laboratories
2) High resolution digital topographic (and other?) mapping resources
3) Shared field equipment program
4) Shared data base management
5) National laboratory for Experimental Surface Process Dynamics.
While motivated by this initiative, these five facilities would be shared NSF-wide and will serve as a significant source of stimulation and resource for the earth sciences community.
I. Whole Basin Dynamics — a community initiative in surficial processes
Introduction. Landscapes are inherently dynamic. On the time scale of years, individual floods, storms, and landslides cause local changes in Earth’s surface and significant damage to human life and property. Over longer time scales, the net effect of such processes is to sculpt the landscape. Landscape dynamics fundamentally reflects mass fluxes not only of sediment but also of surface and groundwater; and of chemicals carried in the water and on particles, and precipitated as chemogenic or biogenic sediment.
The evolution of landscapes is in itself a basic problem in Earth science. It is also fundamentally linked to tectonics, which supplies material to the surface to be eroded. In recent years it has become clear that a strong feedback exists: erosional removal plays a major role in driving and/or focusing tectonically driven rock uplift. At least in some places, rock is drawn toward to the surface from above as much as it is pushed up from beneath. Finally, landscape evolution also has major practical dimensions, particularly as society attempts to predict the consequences of potential anthropogenic climate changes.
What tools currently exist for quantitative prediction of landscape evolution? A planner looking to answer this would be met with an array of largely unrelated and largely untested models dealing with various parts of the landscape. For example, considerable effort has been invested in the study of short-term sediment ttransport through river channels, the main conduits of sediment movement throught he landscape. Methods now exist for estimating sediment fluxes down river channels for known flow conditions, but we have only begun working on how to apply these synthetically over time scales beyond an individual flood. A plethora of erosional-landscape evolution models of great conceptual value remain largely unconstrained by real data. We know very little about overall fluxes of sediment from hillslopes into channel systems. We know very little about mean fluxes of material into and out of floodplains. We can as yet make only rudimentary predictions about changes in the form of fluvial channels, with their attendant effects on transport capacity and sediment storage. We do not have good models for how other transport processes (e.g., eolian) work on their own and interact with fluvial transport. We have a number of very broad-scale models that deal with depositional topography and the stratigraphic record, but again they are largely untested and are not integrated with models of the erosional portion of the landscape. We are only beginning to learn how all of these processes are mediated by the biota. And we have only the beginnings of models for the formation of chemogenic and biogenic sediments.
Here we present a community initiative to fill in some of the gaps in our current understanding. The key elements are:
1. a commitment to measuring critical mass fluxes throughout a small set of carefully chosen transport systems over time spans long enough to include numerous transport events and hence long enough to characterize the response to the full probability distribution of events;
2. a focus on an analytical, quantitative approach to measuring and understanding transport processes;
3. a commitment to an integrated view of the geomorphic system that would include key biological, chemical, and physical processes and hence would involve the physical geomorphology, low-temperature geochemistry, groundwater, and ecology communities;
4. a focus on integrating direct flux measurements with time-averaged measures of erosion and deposition in the system, which calls for a cooperative effort between the above groups and the Quaternary-stratigraphy community;
5. a commitment to use the field and experimental data as a springboard to begin work on community landscape evolution models, analogous to GCMs, that could be used as general predictive tools to answer questions of both scientific and social interest.
The concept of a "basin". The Earth’s surface can be divided into units within which sediment is conserved. We use the term "basin" loosely to mean such a naturally bounded area. For example, for a river system that takes sediment generated within a particular erosional watershed, and deposits it in a lake, the basin would be the watershed, the river system, and the lake. Since fluvial transport is driven by gravity and occurs within distinct channel systems, fluvial basins can be defined, at least to a first approximation, using topography. Although a basin so defined may be open to some transport processes (e.g. wind, groundwater), it is still a geomorphically useful unit, encompassing the main mass sources and sinks. We will therefore focus our attention on fluvial basins.
Choice of field sites. It is not our goal here to prescribe specific field sites where Whole Basin Dynamics studies could be carried out, but we suggest some general characteristics that field sites might have:
·
Manageable scale. An extremely small system, such as a single gully and a small fan, would not include a sufficiently wide spectrum of processes to promote or to encourage generalization. On the other hand, a continental scale system is logistically too difficultfor initial efforts.·
Active tectonics. To emphasize the link with tectonics, at least some field sites should be in areas with active tectonic uplift and subsidence. Such sites would allow exploration of the time scales over which mountain erosion achieves rough balance with uplift. The linkages between mountain erosion and transportation of the eroded debris across the foreland must be forged. Deflections of geomorphic markers such as terraces and Quaternary dating methods can be used to document the tectonic signal.·
Closure with respect to sediment. As mentioned above, it is probably not realistic to insist on perfect closure with respect to any transport process in natural basins. Nonetheless, completion of a sediment budget would be easiest in a system characterized by an overall mass balance between erosion and deposition.·
Variation in transport mechanism.Fluvial transport is the predominant mechanism of mass transfer, and analytical understanding of fluvial mechanics is advanced relative to other transport processes. We will therefore emphasize fluvial systems. However, we also foresee considering field sites with at least some component of eolian, glacial, or subaqeous transport. The connection between fluvial and hillslope processes is of central concern, as the linked system dictates the manner and quantity of mass delivery to depositional systems. The style and rate of hillslope processes will vary strongly from one field site to another.·
Well characterized vegetation The type and amount of vegetation influences in important ways not only the geomorphic processes operating in a basin, but their rates. It is critical not only to be aware of the role of vegetation in the observed process rates, but also of the vegetation history of a study site. For instance removal of trees by logging or for agricultural purposes has long-lasting effects on sediment delivery off of hillsides. Vegetation succession in the forelands of retreating glaciers influences both the biogeochemistry and sediment yields from basins. Vegetative dynamics may well play a key role in setting the lags between climatic events and the sedimentary response of the system. We welcome interactions with the biological community in developing both better empirical data sets and a theoretical understanding of these dynamics.
Time scales and integration with Quaternary geology. The range of time scales under consideration essentially spans that between short-term "engineering-type" studies (100 years) and the high-resolution end of the long-term stratigraphic record (106 years). An absolutely crucial part of this initiative would be close cooperation between the quantitative geomorphology community and the Quaternary geology community. The stratigraphic dimension of the initiative provides the crucial link between necessarily short-term flux measurements and long-term average rates of accumulation. Cosmogenic-isotope studies have the potential to provide timing in the landscape over concommitant timescales.
The stratigraphic work also connects this research initiative with the main (pre-Quaternary) stratigraphic record. This could be of great benefit in terms of both linking the work to the broader Earth sciences community and providing potential new avenues for industrial cooperation.
Modeling. While it would not be appropriate here to discuss the details of how a community landscape evolution model would be constructed, there are some general points to be made:
·
Community landscape models would vary with respect to time and spatial scales addressed, but would have common elements, at least conceptually. Every effort would be made to unify varying approaches, and to encourage modular structure so that improved representations of particular processes could be readily incorporated;·
The scope of integrated models would be ambitious and would seek to include biological, chemical, and physical processes;·
As discussed above, there are major pieces missing from a complete fluvial mass-balance model, and both field and experimental studies are required to develop these;·
This initiative entails a commitment on the part of the surface-processes community to work on standardized interfaces and programming protocols for computer modeling that is at present being done piecemeal
Organization of the project within NSF. This initiative is being proposed as a new direction for surficial processes at NSF. It is in no sense intended as competition for existing programs in the G&P purview, but rather as a bold new step that represents a level of community interaction and commitment to integrated research that has never occurred in the surficial-processes community before. We believe that an initiative like this would lead to new understanding that will be truly greater than the sum of its parts. Doing this requires that everyone sacrifice to some degree her or his favorite project or area in the spirit of collaboration. As much critical and worthwhile science would inevitably be left out of an effort focused on only a few field sites, it is crucial that funding of smaller scale research continue through normal NSF channels at current to enhanced levels. We fully expect that the larger projects will spawn smaller more focused projects designed to answer single-process questions.
While it is not our goal here to prescribe the precise organizational mechanism of this initiative, we note that there is potentially much to learn from the structure of the ONR STRATAFORM program. This is an ongoing, multidisciplinary program involving many PIs that has set out to link process dynamics studies with studies of Holocene deposition patterns on the continental shelf. It involves modeling, experimentation, and multi-year field work at two continental-shelf sites.
II. Sustainable Landscapes. Landscapes at the human timescale
This program is motivated by the need to develop the science to restore and protect landscape functions in order to sustain natural resource use (e.g., land, water, fish, and timber) and ecosystem functionality. Under the urgency created by documented or anticipated ecosystem decline, large-scale and costly decisions are being made about landscape management with the intended consequence of environmental improvement or protection. Commonly, these decisions are being made with little or no scientific basis. Normally these decisions presume that if the physical function of the system is restored toward the pre-landuse state, that the ecosystem function will be recovered. We lack, however, theoretical frameworks and field data to predict landscape change. For example, in the case of linkages between hillslope and river channel characteristics, we lack a theory for landscape erosion and discharge to channels, a theory for sediment routing through the river network, and a theory for channel morphology and its dependence on sediment supply, stream discharge and biotic interactions. We are unable to answer some of the most important questions about landscape processes. This void is currently filled with a chaotic array of empirical and untested, often unverifiable models that are built for specific sites and are then blindly applied to others. Government agencies, attempting to provide sound regulatory authority, are numbed by contradictory, inadequate models and empiricisms that force them often to take best guesses. The general public is well aware of this situation, which serves to diminish the confidence in both the regulatory agencies and the scientific community in general.
This program is conceived as an effort to enable a community-wide focus on building theoretical tools, obtaining fundamental field data and communicating advances in technologies to practitioners. It also will have a strong educational component, as landuse and ecosystem function has wide appeal to students, and provides a great opportunity to see and participate in the development and application of science.
The emphasis on community-wide development arises from the need to consolidate efforts, establish standards of measurement, and develop widely applicable models that have been subjected to careful and thorough testing. The work requires expertise from a broad array of fields and is beyond the scope of a single individual or small group of investigators. While single investigator proposals should be considered, emphasis should be placed on group projects. We see a wonderful potential synergism with the Whole Basin Dynamic initiative both in theoretical and field tool development and in group field studies.
This new program is to be distinguished from other existing programs, most notably the EPA-NSF Water and Watersheds program, which focuses on combining physical, biological and planning understanding for watershed management decisions. The proposed Sustainable Landscapes program, while squarely motivated by societal needs, focuses on the fundamental scientific studies needed to build a platform of understanding and does not attempt to bring in socio-economic considerations. While important in decision making, there remains a deep need for basic research to address the many unresolved problems in landscape processes.
The Sustainable Landscapes program will have three components based on the time frame of interest.
1) Reference landscape: theoretical construct that should emerge from the Whole Basin Dynamics
2) Landscape forecasting: storm event - based predictions of runoff and erosion that can lead to the prediction of landslide and flood hazards
3) Landscape prediction: long-term (decadal to century) prediction of the landscape processes and functions under various landuse and global climate change pressures.
Potential for fruitful collaborations:
Within the landscape prediction component of the initiative, we propose a "2050 project" to predict major landscape changes that would occur in the face of the doubling of C02. This exercise would necessarily involve collaboration with the hydrological and global climate modeling communities for constraint on realistic meteorological forcing scenarios, and with policy experts and planners for constraint on future landuse scenarios.
Industrial collaborations: At both forecasting and prediction time scales, there is great opportunity for interaction with industry, e.g., hydro-power and insurance. Contributions from industry, and collaboration with industry scientists will be fostered by attention to industry specific needs.
Ties to ecology: At these time scales, there are great opportunities for joint research between biologists and physical scientists. Such ties should be promoted rather than avoided.
Ties to the Hydrological Research Facility initiative: Clearly, there should be significant cooperation between the surface processes and hydrological communities in designing and running the proposed research facility. It is the hydrologic response of the landscape that drives most surface processes, and the important feedbacks between surface processes, both physical and biological, that should be documented at the research facility.
B. Comparative Geomorphology
While we have defined a clear case for the launching of the major initiatives on terrestrial landscapes described above, we emphasize here the potential for tremendous growth of our knowledge of other landscapes, in particular those on the remaining Frontiers: submarine and planetary geomorphology. In the last decade, much progress has been made toward understanding tectonically active landscapes through a focus on the geomorphology - geodynamics connection. Analogously, we feel great potential for novel and exciting research exists at the join between geomorphologya nd planetary sciences.
The subaqueous landscape on Earth and the surfaces of other planetary objects within the solar system represent natural geomorphic experiments conducted under radically different environmental conditions. The values of the fundamental variables of these systems, including gravitational acceleration, the densities and chemistries of fluids involved, the surface materials themselves, and the flexural strength of the lithosphere, differ substantially from those in the terrestrial sphere. These surfaces have also experienced radically different climate histories. Yet the fundamental physical laws governing the processes by which these surfaces evolve are the same. Mass, momentum and energy are conserved. The identification and explanation of the diverse topographic expressions of these underlying common laws represents an exciting new challenge to the geomorphic community.
The growing database
We can now begin to satisfy our curiosity about what these environments look like. Massive new collections of planetary and submarine data have already been accumulated. These data sets will be augmented significantly in the next two decades, as technologies evolve and as existing and planned missions complete their tasks. To date, there is little sophistication in the interpretation of these remotely sensed data. The first step is to interpret rigorously the imagery that streams back, and to assess the range of new and different manifestations of surface processes. Each of these represent challenges to our understanding of the surface evolution. We also emphasize that access to this growing data base must be made easy and inexpensive.
The modeling challenge
The next step is the development of conceptual and quantitative models that are flexible enough and broadly targeted enough to encompass both terrestrial and other-world cases. While understanding a foreign landscape is an important target, such studies will also provide unambiguous and rigorous tests of our understanding of the fundamental physics responsible for the terrestrial landforms with which we are more familiar.
Funding opportunities.
The success of this endeavor hinges upon the interaction of scientists in several disciplines, who might not otherwise communicate with one another. The financial burden on any single program can be lightened by tapping different funding agencies (e.g., NOAA, ONR, NASA and NSF) and different divisions within NSF (e.g., MGG, EAR, OCE).
C. INFRASTRUCTURAL SUPPORT
Chronology
Chronology is fundamental to understanding the rates of change and for correlation of events separated geographically . If a significant change occurs in a landscape, was it a part of a global event, or was it strictly regional in scope? The only way to address this question is through accurate chronological control. All the analyses conducted on a sediment core retrieved from a lake, or a cave, are meaningless until they are put in the context of time. Studies done at millennial scale reveals long-time scale changes in landscape. Sometimes, the records suggest little change beyond the well-known early to mid-Holocene shifts in aridity, and the return to a wetter climate during the late Holocene. However, when the same sediment core is picked apart and studied at decadal resolution, an entirely different portrait of biological and physical landscape evolution may emerge. We become aware that the landscape was subjected to multiple nested drought cycles decades to centuries in duration. To what degree are these drought cycles correlated around the world? How rapid is their onset? Is it the case, as some are now suggesting, that the same millennial scale climatic fluctuations that punctuated the last glacial maximum persist even in the absence of the influence of large North American ice sheets? El Niņo influences on the climate can be documented at this higher resolution. Flood frequencies cannot be studied adequately without reliable dates from multiple sites within a flood plain or overbank deposits. This latter issue is of increasing interest both to FEMA and to insurance companies; this information and a strong hydrological modeling context for prediction of flood stages must ultimately be the basis on which decisions are made about whether or not to allow rebuilding after a flood event. Without good chronological control, these questions cannot be asked, and these discoveries cannot be made.
The standard chronological tool of choice, the AMS 14C dates, have well-known plateaus when the D14C of the atmospheric CO2 was different. Correlation with dendrochronology has made the calibration of 14C ages to calendar ages fairly reliable back to the Last Glacial maximum (LGM, 18k calendar years), but this effort must be continued. 14C ages vary by as much as 3000 years from calendar dates at this time scale, making correlation of 14C -dated records with other records based on calendar years (e.g., Greenland ice cores) difficult. This means that we are not adequately equipped to address the issue of synchroneity of events observed in terrestrial records beyond the LGM.
The present bottleneck
Because of the transition between conventional radiocarbon dating and AMS methods, today’s demand for AMS dates far exceeds the ability of the existing labs to produce them. The bottle neck is typically in the 14C graphite target preparation. There is a crying need to support labs that prepare the targets, especially for materials that require specialized pretreatment such as fossilized bones. The ability to obtain dates in a timely manner is important, since the total length (time duration) of a continuous record, or the timing of a discontinuous record advise and inform the researcher how best to proceed with analysis. If a lake sediment core is only 3 meters long but has a basal date of 30,000 14C years, we can only study events occurring on millennial-scale. If the core is 10 meters long and the basal date is only 5000 14C years, we can easily obtain annual or even seasonal information. When 14C ages are returned after a full year’s wait, precious time has been lost, and many researchers will have been forced to proceed on the analytical program based only on a guess.
Many landscape events cannot be dated by 14C. Cosmogenic isotopes such as the radionuclides 10Be, 26Al and 36Cl, and stable 3He and 21Ne have revolutionized our understanding of geomorphic processes and climatic timing in high-altitude and arid landscapes. U-series dating has re-energized the study of past sea-level changes, has allowed calibration of the 14C clock beyond the tree ring record, and has provided spectacular chronological control to the study of uplift of tectonically active coastal areas. Fission-track dating has proven useful in studies of long term exhumation, and will likely be involved strongly in studies of long term evolution of mountainous landscapes. The facilities and laboratories engaged in these dating schemes are limited, and the wait for dates can be many months. U-series dating, in particular, is an expertise typically found in individually operated (as opposed to a national facility) laboratories in academia; obtaining dates is impossible without first convincing these researchers into entering into a collaborative relationship.
There are several ways to resolve these problems: among them, establish more distributed dating centers and laboratories; and establish a national chronology facility.
Easy access to funds
One of the frustrations many of us face when attempting to correlate events across space is the lack of well-dated records. There may be records, many of them results of masters thesis projects and older Ph.D. projects. But these records lack chronological control, and have little significance beyond the local pond, bog or a lake. Typically, all we can tell is that the surrounding landscape underwent several changes, but these changes cannot be put into any time frame. The quality of data may be excellent, but they are worthless unless the timing has been established reliably. If some competitive but accessible program could be established to which students working on un-funded projects can apply for funds to obtain appropriate dates, this sorry state of affairs can start to be remedied.
New Methods
It is difficult to obtain good dates on terrestrial records beyond the range of radiocarbon. Several existing methods such as Thermal Luminescence (TL) and Optically Stimulated Luminescence (OSL) have problems of reliability let alone precision. More work is needed to refine these and other emerging techniques such as amino-acid racemization.
Database
The chronological correlation of different records, even when a good set of AMS 14C dates are available, can be problematic. This is because the method of correction to calendar years has varied through time, and the only way to insure the uniform handling of raw data is to have access to the raw data (he original lab analysis numbers). If such information can be archived in a standardized format at a centralized data center (such as NCDC at NOAA), the access can be insured. We suggest that such policy be instituted for all dates and supplementary information gained with public funding, and that it be the responsibility of the dating facilities to contribute this information.
Databases serve a variety of functions. Beyond making data available and easy to query, they provide a format for the collection of data which ensures that all relevant data are collected. The need for global databases is becoming a high priority in many disciplines. NOAA maintains paleoclimate databases. It will be essential to devote funds to database cooperatives; otherwise, important investigator databases will be lost or it will not be possible to update them easily. The structure of these databases should be determined by the community within different disciplines. It will be necessary to fund workshops to develop these structures and timelines for data delivery to these repositories. Thereafter, it is necessary to continue support for database cooperatives that form the interface between the scientific community and the database.
Sample Curation and Archives
Selective samples and relevant data should be preserved in a publicly accessible facility. For many types of materials, natural history museums serve this function. However, for certain types of samples, like lake cores, there are no facilities. These types of facilities would not need to preserve all cores. Of primary interest would be cores from remote areas, deep lakes which require expensive coring equipment, and for areas that may be destroyed and not available in the future.
High resolution digital topographic mapping resources
Topography is the fundamental data set for any and all geomorphic work. Topography is the data set that serves both as the test of a theory of landscape evolution, and as the template on which all surface processes (including those generating landslides and other hazards) is played out. Yet it is surprisingly difficult to obtain high resolution, high quality topography for much of the Earth. Many surface processes are responsive to short wavelength topography of the order of only a few meters wavelength. No governmentally produced data set exists at this resolution. Neither 90m DEMs from the 1° sheets nor the 30m DEMs from 7.5" quadrangles will suffice. This has left the geomorphic community with no recourse but to generate such sets at their own (and hence at NSF or NASA) expense. This entails either very dense and labor-intensive surveying, high-end photogrammetric techniques entailing soft-copy methods, or laser altimetry.
Within the last decade, laser altimetry has come into its own as a tool for generating high resolution DEMs at the 2m scale. This is flown from aircraft, and is used commercially for siting of power lines and the like. At present only a few private companies have this capability, and NASA has one instrument. Examples of the uses of this new technology now includes the mapping of shoreline change in central California during the 1997-98 El Nino year, the mapping of landslide scars in mass wasting-dominated landscapes, and repeat measurements of the the cross section of the Greenland icesheet. All of these investigations have resulted in breath-taking new data whose density and accuracy could not have been achieved without the use of this equipment.
Given the expense of the tool, no PI will purchase and run such a system. We propose that NSF support a facility that enables individual PIs and groups of PIs to collect 2m resolution DEMs relevant to their project in such a way that it is both cost- and time-efficient to do so. At the moment the inertial barrier is simply too high on both counts, meaning that few geomorphologists have access to this sort of data. The data so generated would be made available in an archive for all to use.
At present, entry into the world of remote sensing is expensive both in terms of hardware and software, and in terms of training. Few facilities exist with the luxury of full-time long-lived support of a manager to aid in the training of new users, and to ensure continuity of the program. Most often, graduate students become trained and then leave, generating great periods of down time on the equipment. Finally, imagery remains very expensive, preventing the individual PI from use of this wonderful new set of tools. We suggest that the topography facility could aid in redressing this problem by 1) providing an archive of data collected by any and all government-supported users, and 2) provide training facilities for users of hardware and software.
Shared field equipment program
It is too expensive for single investigators to maintain large stores of equipment for special projects. Such equipment includes drilling equipment, surveying equipment, shallow seismic arrays, current meters, strain meters, rain and snow gauges, pressure transducers, and differential GPS, among others. We view that it would be beneficial to have a central facility that could provide these types of equipment to investigators for their projects. The equipment would be returned either after completion of the project, or after completion of a field season, to be available for others to use. If properly managed, this method would not only be of great assistance to the scientists, it would be cost effective for NSF. Other divisions, like hydrology, anthropology may also want to participate in such an initiative. This arrangement is similar to the IRIS program in seismology, or UNAVCO in GPS studies, where only one type of equipment is managed, and has parallels with the PICO cooperative arrangement for polar equipment.
National Laboratory for Experimental Surface Process Dynamics
At present there exist only a few major experimental facilities for the study of Earth surface processes. These labs are expensive to maintain, and take an entrepreneurial spirit to continue to operate. It is important that these facilities be maintained, and that access to them be open to the entire community on a competitive basis.
We propose a small funding program, with grants renewable on a 5-year term, that would facilitate the kind of open door policy that Saint Anthony Falls has implemented. The large experimental laboratories (including the hydraulics labs at Minnesota, Iowa, Colorado State, Caltech, and Illinois; the mini-watershed labs at Utah State, Purdue) could compete for a few large awards that would suffice to reduce the costs of visiting scientists, as a means of attracting good, collaborative science. This would benefit both the individual investigator, to whom the labs might now appear to be either closed or too expensive to engage in an experiment, and to the labs themselves, who must engage in perpetual battles of justification and search for funding. We emphasize that we can expect many spin-off experimental studies from the proposed initiatives.
D. Education and Outreach
Geomorphology and Quaternary sciences are blessed in being among the most accessible of geosciences, since both fields study the most visible part of the Earth, its surface. Earth surface processes are therefore familiar to most people, and naturally attract the public to the earth sciences.
The findings of the proposed initiatives must be translated into education of the citizens and decision-makers who are in a position to effect change. We are faced with a significantly skeptical public that is often mistrustful of science, and economic forces that of necessity will continue to be driven by short-term goals. At the same time, the recent spate of catastrophic events such as severe storms, hurricanes, tornadoes, and floods, as well as unusual weather patterns, have brought the topic of global change to the forefront of public’s consciousness. The degree to which the effects of these meteorological events have been exacerbated by our having placed outrselves in harm's way, and the degree to which this reflects real change in the climate, can and are being debated.
We must do our part to educate the public about the likely response to global changes, particulalry in the light of records of past responses, and in the framework of process-based theoretical research. The lack of complete concensus among scientists confuses the public. We must convey the concept that science is a process, that our knowledge evolves through critical dialogue, that the scientific community at any one time has opinions that differ, and that this is both normal and healthy.
We see several levels and numerous formats for bringing geomorphology and the Quaternary sciences to the public. Effective visualizations can bring the geomorphic processes to colleges, secondary schools, and the general public via numerous science and natural history museums. Geography and geology introductory textbooks, AGI lab manuals, Encyclopedia Britannica, and municipal museums are logical venues for visualizations packaged in a CD. Working with K-12 educators, some of these visualization efforts can be repackaged for elementary, middle, and high school students. In fact, we propose to work toward adoption of an earth science curriculum by high schools. Attractive introductory-level courses can be offered at college level, aided by a growing number of computer visualizations of data and simulations of geomorphic events. For example, efforts are being made to integrate icesheet data with other landscape information so that anyone can "see" the glacial world and how it changed as the ice melted. The same visualizations can be tailored for general public, middle-school, and elementary school children. IGERT and STC programs are designed to create a pipeline for future geoscientists and geoscience teachers of K-12. There is an urgent need in the short term to educate the public and the political and economic decision makers, and in the long term to develop a rigorous and stimulating Geoscience curriculum in high schools.
As a part of the outreach effort, the community could establish a hazards program: something in which the community is rapidly alerted of geomorphologically interesting phenomena, for which rapid response funding is readily available. We should attempt to anticipate the effects of predictable events (e.g., El Popo -- see January 1999 National Geographic). And we should be able to get into the affected areas rapidly after an unexpected event (e.g., Hurricane Mitch), with the possibility of obtaining longer term funding to watch the evolution of the natural perturbation.
Any serious effort to use broadcast media to take this science to the public should be supported strongly.
In addition, the initiatives we have proposed have major implications for civil and environmental engineering. What we learn from the Predictive Earth Surface Dynamics initiative will be shared with working engineers in a series of workshops and short courses offered at professional meetings. Information will then be disseminated to appropriate municipal offices through these channels. In addition, basins being studied by large groups of researchers in the Whole Basin Dynamics initiative could provide ideal sites for K-12 teacher training programs and focuses for REU sites. The more the students are taken to the field, to rub shoulders with researchers and to see the process of science in its early stages, the better. We need to take advantage of all opportunities to accomplish this.
Feb 6/7, 1999
Workshop participants
Quaternary Science and Geomorphology
Robert S. Anderson
Earth Sciences Board
UCSC
Santa Cruz, CA 95064
831-459-3342; fax 831-459-3074
rsand@earthsci.ucsc.edu
Allan Ashworth
Geosciences Department
North Dakota State University
P.O. Box 5517
Fargo, ND 58105-5517
701-231-7919; 701-231-7149 (fax)
ashworth@plains.nodak.edu
Thure Cerling
Department of Geology and Geophysics
University of Utah
Salt lake City, UT 84112
tcerling@mines.utah.edu
801-581-7065 fax; 801-581-5558; 801-581-7062
Peter U. Clark
Dept of Geosciences
104 Wilkinson Hall
Oregon State University
Crvallis, OR 97331
clarkp@ucs.orst.edu
541-737-1247; 541-737-1200 fax
Bill Dietrich
Department of Geology and Geophysics
University of California, Berkeley
Berkeley, CA 94720bill@geomorph.berkeley.edu
510-642-2633; 510-643-9980 fax
Russ Graham
Dept of Earth & Space Sciences
Denver Museum of Natural history
2001 Colorado Blvd
Denver, CO 80205
303-370-8363; 303-331-6492 fax,
rgraham@dmnh.org
Eric C. Grimm
Illinois State Museum
Research and Collections Center
1011 East Ash Street
Springfield, IL 62703
217-785-4846; 217-785-2857 fax
grimm@museum.state.il.us
Vance Holliday
Dept geography
University of Wisconsin
550 N. Park St.
Madison, WI 53706
608-262-6300; 608-265-3991 fax vthollid@facstaff.wisc.edu
Emi Ito
Dept Geology and Geophysics
University of Minnesota
310 Pillsbury DR., SE
Minneapolis, MN 55455
eito@umn.edu
612-624-7881; 612-625-3819 fax
Jim Knox
Dept Geography
University of Wisconsin
550 N. Park St.
Madison, WI 53706-1491
608-262-1804; 608-265-3991 fax
knox@geography.wisc.edu
Charles (Jack) Oviatt
Dept of Geology
Kansas State University
Manhattan, KS 66506
joviatt@ksu.edu
913-532-6724; 913-532-5159 fax
Chris Paola
Dept Geology and Geophysics
University of Minnesota
310 Pillsbury DR., SE
Minneapolis, MN 55455
cpaola@tc.umn.edu
612-624-8025; 612-625-3819 fax
Liz Safran
Earth Sciences Board
UCSC
Santa Cruz, CA 95064
lsafran@es.ucsc.edu
831-459-3082; 831-459-3074 fax