March/April 1997


I believe the answer to this question is yes, although I'm not sure how many scientists would agree. For example, I suspect that most of my MIT colleagues in physics, chemistry, and biology would characterize earthquake studies as a strictly applied science. They would quickly concede, of course, that the study of earthquakes has been stunningly successful as an applied science. Many of them appreciate the remarkable progress in mapping active faults and characterizing the paleoseismic history of regions like Southern California and the Pacific Northwest, and some are aware of the improved capability for the rapid collection, analysis, and dissemination of seismological data following a damaging earthquake. On the other hand, the older among them probably know that the overall achievements in applied earthquake science have not yet matched the high expectations of three decades ago, when it appeared that short-term earthquake prediction might be right around the corner.

Following the damage caused by the great 1964 Alaskan earthquake, a select committee chaired by Frank Press issued a report entitled Earthquake Prediction: A Proposal for a Ten-year Program of Research (White House Office of Science and Technology, 1965). The optimism reflected in the title of this report was heightened in the early 1970's by the apparent successes of some empirical prediction schemes and the plausibility of the physical-process models (e.g., dilatancy diffusion) upon which they were based. By 1976 a distinguished panel of earthquake scientists convened by the National Research Council's Committee on Seismology was willing to state: "The Panel unanimously believes that reliable earthquake prediction is an achievable goal. We will probably predict an earthquake of at least magnitude 5 in California within the next five years in a scientifically sound way and with a sufficiently small space and time uncertainty to allow public acceptance and effective response."

Although more than one hundred earthquakes have occurred in California with magnitudes greater than 5.0 in the intervening twenty years, this promise remains unfulfilled. In fact, the observations in California and other well instrumented areas like Japan have been disheartening. Previously proposed schemes for short-term earthquake prediction have not proven to be successful, and despite the substantial increase in monitoring capability, no unambiguous precursory signals have been identified that are diagnostic in the sense required for useful short-term prediction.

The collapse of earthquake prediction as a unifying theme and driving force behind earthquake science has caused a deep crisis. One reaction has been to declare that the predictability issue is essentially solved: While some long-term aspects of earthquake activity can be forecast probabilistically, earthquakes in general are just not predictable in the sense of the term understood and desired by the general public, i.e., close bounds on the locations, times, and sizes of individual large earthquakes. This contention is based on the notion that active fault systems are chaotic; that knowing the state of the system even very precisely at one instant, say at the time an earthquake is nucleating, is not sufficient to predict its behavior just a short time later--e.g., how big the nucleating earthquake will get before the rupture stops. While this thinking may apply to some classes of earthquakes, such as intermediate-sized events in California, it would be premature to generalize the behavior to all large earthquakes. A more prudent statement is that we still don't know how to answer the question, "Which types of earthquakes, if any, are short-term predictable?" Having said that, we can hardly maintain an optimistic attitude toward the feasibility of deterministic prediction, at least in the short term.

What, then, are the issues that should drive earthquake science? There is, of course, a menu of interesting problems related to the practical aspects of hazards mitigation that we can and should be solving, such as improving the technologies for real-time seismology and rapid response, predicting the strong ground motions for major events, and using modern geological and geodetic techniques for refining seismic hazard maps. These problems are scientifically challenging in their own right, and their importance to our globalized society is beyond dispute. The practical study of earthquakes is a healthy and vigorous applied science that continues to deserve strong support from the federal funding agencies.

But the applied-science menu is too meager a diet for sustaining earthquake research as a whole. For example, the best and brightest students are not likely to be attracted to a strictly applied science that is primarily a consulting service for engineers (which is, unfortunately, the current situation in the environmental earth sciences). Our prospective young researchers would find it pretty glum if they were looking forward to scientific careers dominated by the task of microzonation. Moreover, the public would quickly lose interest in such a pedestrian enterprise. To remain healthy, earthquake science must be draw from the essential issues of basic science.

A precise definition of basic science is elusive, but three of its functions are clear. The first is to provide the knowledge base needed to improve the methodologies of applied science, in this case the practical aspects of earthquake hazard mitigation, which is itself a broad mandate for doing all kinds of interesting research. Take, for example, the difficult problem of seismic wave scattering in heterogeneous, anisotropic media like the Earth's crust and upper mantle, which happens to be a subject of my own recent research; I can argue that this work, although quite removed from the central issues of earthquake hazards, might eventually improve algorithms for imaging rupture processes or models for predicting strong ground motions. Such a long-term, knowledge-based strategy was adopted twenty years ago in setting up the National Earthquake Hazard Reduction Program, and it has proven to be enormously successful in delivering practical benefits. Given the recent external criticisms of NEHRP, the earthquake-research community should assert this point more aggressively. A powerful case can and should be made for a fundamental approach to the earthquake hazard problem, especially in the arena of assessing hazard potential.

The second function of basic science is to improve fundamental understanding in a way that contributes to other areas of applied and basic science. For example, the laboratory study of earthquake fracture mechanics and fault friction has led to dynamical models and constitutive relations that are being applied in materials engineering. Today, the theoretical investigation of episodic deformation is addressing the fundamental problem of strain localization in the lithospheres of the Earth and other terrestrial planets. And we should not forget the profound role that earthquake science played in the plate tectonic revolution, which counts as one of the major accomplishments of twentieth-century science. Earthquake studies will continue in this role as a basic component of the geosciences.

It is more difficult to maintain that earthquake science is somehow fundamental to science in general, but let me try to make this case. The key to this argument is the recognition that the spectrum of basic science ranges between two extremes. One side is the goal of reductionism, that grand march begun 400 years ago toward discovering the fundamental laws of the universe. The reductionist program seeks to take apart the complexity of the world and reduce it to simple statements about fundamental forces and, ultimately, to intrinsic symmetries. This grand march continues, although to many, myself included, it appears to be receding into the shadows of the unobservable. At the other end of the scientific spectrum lies the goal of understanding the very complex systems of the natural world, which can be grouped according to their proximity and their scale; they range from the biosystems of individual organisms and the ecosystems of groups of organisms, to the geosystems of the Earth and the other planets, outward to the astrosystems of the stars and the galaxies beyond. The scientific approach to the study of natural systems that is most in line with the reductionist agenda is the so-called "constructionist program," which can be summarized as follows: From the fundamental laws that characterize the basic processes among the elements of the system, we seek to describe quantitatively the essential aspects of the system's behavior. One of the great disappointments of reductionism has been the conceptual failure of this approach. In 1972, Philip Anderson wrote an article in Science entitled "More Is Different" in which he asserted: "The reductionist hypothesis does not by any means imply a 'constructionist' one: The ability to reduce everything to simple fundamental laws does not imply the ability to start from those laws and reconstruct the universe. In fact, the more the elementary-particle physicists tell us about the nature of fundamental laws, the less relevance they seem to have to the very real problems of the rest of science, much less to those of society. The constructionist hypothesis breaks down when confronted with the twin difficulties of scale and complexity."

This failure is rooted in what the philosophers of science call ontological decoupling. Silvan Schweber, a historian of science writing in the November 1993 issue of Physics Today, described the situation as follows: "The reductionist approach that has been the hallmark of theoretical physics in the 20th century is being superseded by the investigation of emergent phenomena. ... These conceptual developments ... have revealed a hierarchical structure of the physical world. Each layer of the hierarchy is successfully represented while remaining largely decoupled from other layers."

In other words, each level of science has its own "fundamental", though usually approximate, equations. But knowing these equations is not enough, because it is not the equations but their solutions that provide mathematical descriptions of physical phenomena. "Emergence" refers to the properties of the solutions that are not readily apparent from the equations themselves, a prime example being deterministic chaos.

Geosystems, ranging from the global systems of climate, mantle convection, and the geodynamo to more localized systems like petroleum reservoirs, hurricanes, and active fault systems, provide some of the best examples of emergent phenomena. The first systematic treatment of chaos in a dissipative system was Ed Lorenz's 1963 paper, "Deterministic Nonperiodic Flow", which investigated simple models of atmospheric convection. Systems concepts like universality and self-organized criticality, which have been applied in a prominent way by physicists and geophysicists to earthquake phenomena, have proliferated into a vast array of buzzwords, heralding the synthesis of a new science of complex systems.

Now, when a physicist talks about a complex system, she's usually referring to a very simple system that exhibits complex behavior. Geosystems are truly complex in that they lie way beyond what we might call the "constructionist frontier", and they therefore present special, unsolved problems of observation, analysis, and inference. Earthquake science should be able to lead the intellectual development at this end of the scientific spectrum. Look at the competition. Biology certainly has a legitimate claim to complexity, but most of biology is now preoccupied with a reductionist-constructionist program that sees organisms as implementations of the genetic code. Indeed, modern molecular biology is the science where the constructionist agenda has been the most successful, because the master molecule, DNA, provides an essentially deterministic template for the most fundamental biological processes. The nonconstructionists--e.g., ecologists and evolutionary biologists--have been marginalized, their efforts judged largely on how much they employ modern genetic methodologies. Or take the science of astronomy. Astrosystems are manifestly complex, but the problems that astrophysicists consider to be the most important are those of cosmology, i.e., the ones most directly connected to fundamental physics. Many astrophysicists are thus coopted by the old reductionist program.

The current situation presents us with an unusual opportunity for scientific leadership. In fact, the sheer intransigence of the problems we face in the study of earthquakes leaves us no choice but to extend the limits of science. Fault systems are among the most vexing geosystems to model because the essential dynamics of fault interactions involve such a wide range of spatial and temporal scales. Furthermore, they are largely opaque. In comparison, the climate system, though immensely complicated, is fairly transparent and accessible to observation. How do you progress toward understanding a geosystem for which the data are so incomplete and inaccurate and where most of the system is hidden from view? This ignorance forces us to develop new technologies for remote sensing, new methods for inversion and data assimilation, and new concepts in the theory of inference. It pushes us toward the scientific frontier.

Crucial to this endeavor is the question of predictability, because the continuing prediction of a geosystem's behavior is the truest measure of how well it is understood. I'm not here referring narrowly to earthquake prediction but more generally to the ability to simulate a priori the full range of behaviors of active fault systems and to know which aspects of these behaviors are most deterministic. The methods for investigating geosystem predictability are very primitive, and there is ample room for seminal breakthroughs that could have wide application to other natural systems. We must advance this line of inquiry more quickly.

This brings me to the third function of basic science, which is to enlighten humanity about its place in the world. It is no accident that astronomy and evolutionary biology are the two most popular sciences; they are valued by the general public precisely because they provide a physical and temporal context for our civilization. Our job as earthquake scientists is certainly tougher in this respect than that of the astronomer or dinosaur specialist, since large earthquakes are usually an unexpected form of very bad news. Nevertheless, it is our responsibility to provide a rational context for living on a restless Earth governed by natural forces that can never be totally understood and are certainly beyond our control. To hear the need for this perspective, listen to Bill McKibben complain in his book The End of Nature: "... about the sadness of a world where there is no escaping man. Although for decades civilization has pillaged and polluted the Earth, in the past those attacks were relatively localized; now, with the global changes caused by greenhouse gases and ozone erosion, man has altered the most elemental process of life everywhere, and the outdoors, nature itself, has been turned into the equivalent of an enormous heated room. The basic forces of nature, once beyond man's reach, will forever more be subjects of man's domination."

McKibben's vision reminds me of Isaac Asimov's description of Trantor, the Earth-like planet that was the center of the Galactic Empire in the Foundation Trilogy. It was a passive, dead planet completely sheathed in an encircling megalopolis, where sentient beings controlled everything and the basic forces of nature were nowhere to be seen. In contrast, our Earth is very much alive, geologically speaking, and its internal forces can never be mastered! A significant role for the earthquake scientist is to help human society adapt to this reality.

I close with a direct appeal to young scientists who aspire to study earthquakes. You are fortunate to have chosen a field where the distance between basic and applied science is remarkably short. The pursuit of either aspect can lead to an immensely rewarding and satisfying career. However, to fully exploit the opportunities outlined in this article, you must become deep-thinking individuals, capable of delving into the most fundamental aspects of earthquake phenomena. While you should seek to apply your skills to the practical issues of hazard mitigation, you should try to avoid the parochialism of a narrowly applied science. Go for the big problems, answer the difficult questions that are the true challenges of earthquake science. The NRC has recently commissioned a Committee on the Science of Earthquakes, which I chair, to articulate these challenges and to argue for the resources that you will require. In this endeavor, we need your help. Think about these questions and let me know your thoughts.

Thomas H. Jordan
Department of Earth, Atmospheric, and Planetary Sciences
Massachusetts Institute of Technology
Cambridge, MA 02139, USA
e-mail: thj@mit.edu

To send a letter to the editor regarding this opinion or to write your own opinion, contact Editor John Ebel by email or telephone him at (617) 552-8300.

Posted: 18 January 1999