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OPINION WHY IS EARTHQUAKE PREDICTION SO DIFFICULT?
Earthquake predictability has been the subject of several recent, controversial articles within the seismological community. The intensity of the controversy is understandable, since it stems both from our present inability to predict earthquakes and from the potentially great value that prediction could have for society. Our difficulty in predicting earthquakes is partly due to the inherent characteristics of earthquakes and seismic waves and partly to an incomplete understanding of the earthquake process. In order to gain some perspective on this issue, it is useful to place the earthquake problem in the context of other natural hazards. Nearly all other natural hazards, from hurricanes to wildfires to volcanic eruptions, are predictable to some extent. The predictions are based on precursors, defined here as the non-threatening, initial phase of a natural hazard. This precursory phase consists of two parts, the preparation of the disturbance itself and the propagation of that disturbance to population centers. For example, a hurricane represents an atmospheric disturbance that develops at sea in the tropics and subsequently moves slowly toward population centers, at which time it becomes a threat. The precursory phase, including the preparation and propagation times, lasts hours to days. Other weather disturbances, such as tornadoes, occur on much shorter time scales, although the conditions under which tornadoes are highly probable can usually be recognized. In the case of earthquakes, we have yet to observe a reliable preparation phase, and the propagation time is very short, on the order of seconds. Tsunamis possess much longer propagation times, so that forecasting is possible, in the absence of an observed preparation phase. Probably the most closely related hazard to earthquakes is volcanic eruptions. Prediction must often be based solely on identifying a preparation phase because in many cases the propagation time is very short. For volcanic eruptions, however, the preparation phase has a known physical basis, namely the pre-eruption upward transport of magma. This magma transport has several observable manifestations, including crustal deformation, microseismcity, changes in the gas chemistry and increases in the temperature of hydrothermal fluids. Volcano prediction is a reality. Perhaps the most successful prediction was the June, 1991 eruption of Mount Pinatubo (in the Philippines), which led to the evacuation of 80,000 people and saved billions of dollars in U.S. aircraft that were moved from Clark Air Force Base. This volcano had not erupted in 400 years but was predictable from a variety of precursory signals. It is likely that improved monitoring of crustal deformation, seismicity, and other magma-transport indicators will ultimately lead to the routine prediction of volcanic eruptions. Our poor success record in earthquake prediction has understandably produced a shift in emphasis to other aspects of natural disaster reduction. There are clearly things that can be done to reduce the vulnerability to an earthquake hazard, in the absence of predictive capability, and we have made much progress in these areas. We have taken significant steps forward both in mitigation, the long-term actions that reduce the vulnerability to hazards, and preparedness, the short-term actions taken around the time of an event. For example, there have been important efforts to identify those areas that are most prone to sustaining significant earthquake damage (through the generation of hazard maps), so that informed decisions can be made about land use and building codes. Warning systems that detect and immediately broadcast the occurrence of an earthquake help with preparedness and in guiding the emergency response to a disaster, and in special cases can give a few seconds of advanced warning. For the other significant natural hazards, short-term forecasting is an integral component of preparedness. With hurricanes and volcanic eruptions, for example, buildings can be secured, equipment can be removed, emergency services can be put on alert, and populations can be evacuated, if necessary. It is often said in the seismological community that earthquake forecasting would not be valuable, even if it were possible. All we need are stronger buildings to withstand earthquakes. I believe that this sentiment is misguided. Clearly, advanced warning has been extremely valuable for other natural hazards, and such information in the case of earthquakes would be equally valuable. We must ultimately admit that much of this sentiment stems from our frustration over the surprising difficulty of the earthquake prediction problem. Why are earthquakes different from these other hazards? Why are earthquakes the last of the natural hazards to be predictable? For one thing, the short propagation time means that prediction must be based on the existence of a preparation phase. It is clear that we have yet to detect, on a reliable basis, such a preparation phase. Is this because there is no such phase in the case of earthquakes, or because we have not yet observed it? This question is at the heart of the present debate on the predictability of earthquakes. The notion that slow tectonic deformation might precede significant earthquakes, and be detectable by seismic instrumentation, has been around for decades, as illustrated by the quote from Charles Richter's 1958 textbook at the beginning of this article. This still remains, in my opinion, the most likely form of an earthquake preparation phase. Progress, however, has been slow in evaluating this hypothesis and more generally in understanding the deformational context of earthquake occurrence. It is the knowledge of this deformational environment that I believe will fill a major gap in our understanding of earthquakes. In the broadest sense, plate tectonic theory has provided us with the underlying cause of most earthquakes, as due to the relative motion of plates along their boundaries. Yet, we have only begun to explore this relationship, and the most important questions remain unanswered. How does steady plate motion ultimately lead to the occurrence of individual seismic events? Are there transients in plate boundary deformation, as suggested by recent strain/geodetic observations, and if so, what are their spatial and temporal characteristics? Do transients propagate? How do the individual faults within a fault system interact? How do earthquakes interact? And finally, is there an observable preparation phase to earthquakes that may form the basis for prediction? It is becoming increasingly apparent that earthquakes are only the most visible part of a complex system of interactions that we have only begun to explore. In order to more fully understand this system that defines the plate-motion/earthquake relationship, I believe it is necessary to characterize and understand its most easily observable manifestation: plate-boundary deformation. How, then, should we proceed? We can gain insight from other fields that study complex natural phenomena. Without exception, these fields are primarily data driven. Major advances in understanding have followed major increases in monitoring capability. For example, recent advances in meteorology generally, and weather forecasting particularly, were in large part due to the deployment of a multi-billion-dollar satellite system that allows for continuous, global monitoring of atmospheric disturbances. Our greatest limitation in the study of plate-boundary deformation is the lack of adequate monitoring capability. Of course, we have thousands of seismometers that perform the important task of monitoring seismic activity. But these are primarily intended for studying the earthquake process itself, rather than its deformational environment. The earthquake science community needs an adequate facility for the semi-permanent monitoring of the plate-boundary deformation field. A plate boundary deformation network (pbdn) ought to be established that is capable of monitoring deformation along the roughly 1000 km by 200 km segment of the Pacific-North American Plate boundary zone that is dominated by the San Andreas fault system. Such a network should be capable of detecting surface strain spanning the spatial/temporal range defined by plate motion at one end and earthquake rupture at the other: seconds to decades and meters to 100's of kilometers. At present, there is no one seismic/geodetic technique that covers this broad range with adequate sensitivity and dynamic range, and at least two would be required. For example, GPS (or SAR) can cover the long-period (one-month to decades), long-wavelength (>10km) part of this spectrum, while point-strain measurements, such as those obtained by borehole tensor strainmeters, could be used at shorter period (one-hour to one-month) and wavelength, where they enjoy orders of magnitude greater sensitivity. Seismometers can adequately cover periods shorter than one hour. The required instrumentation has already been developed for such a network. GPS (and SAR) technology is now standard. Also, several types of borehole tensor strainmeters are either operational or are in final stages of development. The pbdn should also be able to monitor strain at seismogenic depths, as well as at the surface. This is more relevant to the problem of earthquake occurrence, but far more difficult, because strain cannot be measured directly. Instead, strain indicators, such as microseismicity and temporal variations in elastic properties, must be monitored and 'calibrated' in some way. Many of these indicators can be observed using three-component seismometers. The pbdn would ideally consist of 1000-2000 sites covering the plate boundary zone at roughly 10 km spacing, and each could include, for example, a GPS receiver, a borehole strainmeter, a borehole broadband three-component seismometer and additionally a strong-motion accelerometer for covering the high-frequency, high-amplitude end of deformation. It is encouraging that the GPS/seismometer components of such a network are presently being deployed in Southern California as part of the SCIGN network. In order to adequately fill the sensitivity gap in the one-hour-to-one-month period band, however, it would be necessary augment this configuration with strainmeters. Indeed, most of the published studies of strain transients have used data from these instruments. The major obstacle to deploying such a monitoring network is not technical or logistical, but insufficient resources. It is estimated that the cost of each site would be about $100,000, including a 200-meter-deep hole for the borehole instruments, or about $100 million for the entire network. If viewed as a 20-year experiment, with $10 million/year for maintenance and another $10 million/year for research, this would average out to $25 million/year over the life of the experiment. While this may sound like a large sum to many, it should be put in perspective. As a large facility/research program in the earthquake sciences, it would have a budget comparable to other large programs, such as NEHRP or IRIS. The people of California could entirely support such a program with a contribution of less than a dollar from each resident per year! There has been justifiable concern, which I share, that basing a major earthquake science program solely on earthquake predictability would be very risky, given our lack of success to date in achieving this goal. For this reason, earthquake prediction should be embedded within a rich scientific problem that will generate significant results regardless of whether prediction is ultimately achieved. Plate boundary deformation constitutes such a problem. In its own right, it is an important and relatively unexplored area of plate tectonics that is at the foundation of nearly all active tectonics. Geophysics, and particularly seismology, would play a leading role in such a broad endeavor.
Paul Silver 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: 26 Feb 1998 |