EMF Research Activities Completed Under The Energy Policy Act of 1992 (1995)

The research strategy of the the Electric and Magnetic Fields (EMF) Research and Public Information Dissemination (RAPID) program given in the Research Agenda and Communications Plan (1994) attempts to balance breadth and depth within a limited budget and schedule. Because specific robust experimental systems that can achieve the program goals have not been identified, the selection of projects must be based on a general knowledge of agents that induce cancer, behavioral detriment, or neurotoxic effects and results of previous studies of specific responses observed for systems exposed to EMF. The selection must consider as broad a range of experimental systems as possible within budget constraints. It must be accepted that some, if not most, studies will show no effect. It also must be accepted that false positives and false negatives might result from some of the studies. False positives can be identified through attempts to replicate work in other laboratories. False negatives are often difficult to identify, although this problem can be partly overcome by obtaining sufficient depth in study areas suggested through hypothesis-driven research.

Generally, the research strategy for the EMF-RAPID program is designed to achieve the goals outlined by the Energy Policy Act of 1992 and to achieve an acceptable balance between depth and breadth. This committee found no glaring omissions in the program. The program must, however, include mechanisms for seeking rapid confirmation of important observations and for the rapid implementation of studies that seek to test new hypotheses that appear especially relevant.

The research agenda brings together appropriate government agencies with history and expertise in the issue. It appears to be focusing on resolving inconsistencies in previously reported end points sensitive to field exposure rather than on implementing a broad general screening study. Given the years of research already dedicated to the issue, the stated approach is welcome.

The introductory chapter of the EMF-RAPID program document (Research Agenda and Communications Plan, 1994) states three specific goals for the program: Determine whether exposure to EMF produced by the generation, transmission, and use of electric energy affects human health; carry out research, development, and demonstration of technologies that would mitigate any adverse human health effects; and provide for the collection, compilation, publication, and dissemination of scientifically valid information to the public.

A definitive answer to the first goal—determining whether exposure to EMF produced by electric power systems or electric-power-consuming devices constitutes a public health hazard —is in all likelihood not achievable within the limitations of the 5-year program established by Congress. Research addressing this question has been under way since the mid-1970s, and there are no indications that it is near resolution. The goal is problematic for two basic reasons: First, it is never possible to prove conclusively that there is no risk, and second, one cannot prove conclusively that one or two identified adverse effects are the only factors contributing to the risks considered. A more rational interpretation of this goal is stated in the Program Focus section of the EMF-RAPID document (Research Agenda and Communication Plan, 1994, pp. 2). In that section, the program is said to “adopt the hypothesis that exposure to electric or magnetic fields under some conditions may lead to unacceptable risk to human health.” The goal of the program is then restated as “not only to test, as far as possible within the statutory time limits, that hypothesis for those serious health effects already identified, but to identify as far as possible the special conditions that lead to elevated risk and to recommend measures to manage risk.”

The second goal identified by the EMF-RAPID program focuses on techniques to mitigate risks not yet demonstrated. That might be a reasonable goal in a long-term project permitting sequential research in which risks are first identified and understood, and then methods are devised for mitigating them. This committee questions, however, how productive mitigative research can be if it is forced to proceed concurrently with efforts to identify and quantify health risks.

The third goal, focusing on communication, is considered appropriate because it does not necessarily require successful resolution of the first two goals.

A clear strength of the planned effort is the emphasis on communication. Education of the media and public about the process of scientific research and about issues of relative risk seems essential for reducing public apprehension.

For a program clearly directed toward the performance of a risk assessment for an environmental agent, a clear weakness in the program strategy is the absence of details in the methodology to be used in its risk assessment. This absence decreases the likelihood that proposed studies will yield data that can be incorporated into such an analysis. Important questions must be resolved. For instance, if results are not reproducible, how will this influence the considerations of the risk assessment process? What data are needed to identify the characteristics of exposure that are azardous? How will data on cocarcinogenesis be interpreted? Risk analysis is a precise process, and until the model and methods for the application are defined, it is difficult to assess whether the program could accomplish the risk assessment goal.

In our view, the decision to conduct all biology and health-related research through the National Institutes of Health (NIH) grant process is the most controversial aspect of the program. The NIH investigator-initiated system has made America preeminent in biomedical research, and it is a great system for performance of basic research. However, to make the best use of the program, the committee strongly recommends that a special study section, including some individuals with broad and specific knowledge of EMF, be formed to critically evaluate new and competing renewals of the EMF-RAPID program, particularly with a view toward bringing the program to closure at some reasonable time. This recommendation is made because of the unique nature of the EMF-RAPID program and the need for review by peer-scientists who have a detailed understanding of the EMF field and the unresolved issues involved. The committee believes that, the current austere funding climate, having EMF-based grants reviewed by the NIH Radiation Study Section will severely limit the chances of success of that portion of the EMF-RAPID program funded through the grant

system of NIH. In addition, we recommend that the program office consider selected use of cooperative agreements to allow more focused studies to be performed when needed.

Furthermore, we are concerned that there is no apparent way to resolve the tensions between the goal of answering, within a few years and with a modest amount of research funds, the question “is exposure to EMF safe?” and the realities of scientific research. Stakeholders in the public and private sectors often place inordinate faith in the dual premises that, at the end of the 5-year EMF-RAPID effort, a credible risk assessment process can be completed, and that risk assessment will answer the question of the safety of exposures to environmental EMF. We think it unlikely that sufficient data and knowledge will be acquired in the short time allocated to the performance of the research program to enable the completion of a meaningful risk assessment. Although the EMF-RAPID program provides a great boost to the resources that are needed to conduct important scientific inquiry, and even though the results will contribute markedly to a more thorough understanding of the issues surrounding the search for EMF effects on biologic systems, it is unlikely this program alone will provide the definitive answer to the questions concerning the possible EMF hazards. It is unrealistic to believe science will deliver or demand, even if ample resources were provided (this sentence will be deleted from final report). Based on the delays in establishing this program and the time constraints inherent in the grants process, the committee strongly recommends that the Congress consider extending the program to at least 1999. The additional time is needed to ensure timely completion of the projects that are still to begin and to seek mechanistic insights about any positive effects that are observed in the preliminary results of the research.

Strategically, the EMF-RAPID program has placed heavy emphasis on reproducibility of previous measurements. The initial projects were funded only if their primary focus was reproduction of an effect already described in the literature. Furthermore, given the small size of

the overall effort of the EMF-RAPID program, only a few phenomena were targeted for study. Despite the constraints in time and funding, however, the overall strategy for research in biologic studies contains a relatively broad approach for cultured-cell systems. This is combined with a more specific focus on cocarcinogenesis and melatonin effects in animal studies. Although this strategy has gaps and omissions, it represents a solid middle approach; it follows the most intriguing data and the most reasonable hypotheses. It must be accepted, however, that over the remaining time for the proposed studies, it is unlikely that a sufficient data base can be produced for a formal risk analysis, unless of course, the risk is perceived to be not of concern.