Health Effects of Electric and Magnetic Fields: Are We Done Yet?

Savitz, David A.

In Brief

“… the burden is on the authors to make a case that their question is worth asking.”

Author Information

From the Department of Epidemiology, University of North Carolina School of Public Health, Chapel Hill, NC.

Address correspondence to: David A. Savitz, Department of Epidemiology, CB # 7435, University of North Carolina School of Public Health, Chapel Hill, North Carolina 27599–7435;

Article Outline

Although seeking causes of disease and looking for consequences of exposure are in many ways parallel research endeavors, there is a key distinction for epidemiologists. Health, not exposure, is the ultimate focus of our research. No matter how frustrated we may become in our search for causes of disease, we should not lose interest in that goal. Surveillance of the potential health impact of exposure has value, but only up to a point. Ideally, once a question has been raised regarding such a potential hazard, the research process would eventually convict or exonerate it, and policy makers could use that information to improve their decisions. However, such resolution is rather rare in practice, and in the absence of such a verdict, how do we know when to stop?

Power-frequency electric and magnetic fields (EMF) have been a prominent topic in environmental epidemiology for nearly 25 years. More recently, radiofrequency radiation, such as that produced by cellular telephones, has been raised as a concern by the public. As scientists, grant reviewers and journal editors, we face decisions about what research directions are worthy of pursuit. Epidemiologic methods lend themselves to evaluating any imaginable consequence of such exposures, without regard to the source of motivation—hypothesized biophysical pathways, prior epidemiologic evidence, public concern or data availability. Before asking about the adequacy of methods and clarity of presentation, we must ask whether the question itself deserves the attention of the research community (or journal space).

In 2002, Epidemiology published papers on the potential effects of personal exposure to EMF on miscarriage, 1,2 exposure through infant incubators and childhood leukemia, 3 occupational exposures and female breast cancer, 4 and radiofrequency radiation in relation to brain and salivary gland cancers. 5 In this issue, Norwegian databases on residence, power lines and births were cleverly and efficiently integrated to address potential effects of EMF on birth defects, with some positive associations and some stronger inverse associations reported. 6 The reviewers and editors agreed that this paper made a contribution to the state of knowledge on EMF and birth defects based on the quality of the data and analysis. However, how likely is it that this line of research is building toward discovery of etiologic relations between EMF and birth defects that might lead to prevention? Beyond the isolated contribution of this study, is there momentum in this line of investigation? In 10 years, will we find that this paper or the others listed above were among the few that initiated an important and productive direction for research, given how rarely such success occurs?

Some potential health consequences of EMF have generated epidemiologic suggestions that are clearly worthy of further pursuit if methods can be found to improve upon the prior studies. The effect of relatively high residential exposures, above 0.2 μT, on childhood leukemia has sufficient momentum 7,8 to be worthy of such effort. In contrast, occupational exposures have been thoroughly evaluated with respect to leukemia and brain cancer. 9 Despite the possibility of a modest association, prospects for further refining our understanding through epidemiology are limited. A hypothesized mechanism 10 and public concern motivated a series of studies on EMF and breast cancer. Although assessment of the value of further research on this issue awaits results of several major studies in progress, epidemiologic research thus far offers little encouragement. 11,12 There is isolated evidence of a potential effect of EMF on miscarriage 1,2 and indications of an association with amyotrophic lateral sclerosis. 13,14 Research that can constructively address those research questions would be welcome.

What about the potential health consequences that have received less attention, such as reproductive outcomes other than miscarriage (including birth defects), childhood and adult cancers other than leukemia and brain cancer, neurodegenerative diseases other than amyotrophic lateral sclerosis, and depression? What about endpoints not yet considered at all, such as infection (attributable to altered immune function), osteoporosis (bone metabolism is affected by electrical charges) or neurodevelopment (disruption of brain development)? Although no biological effects of environmental levels of EMF have been demonstrated, the diversity of effects that could be conjectured is virtually unlimited. Those conversant with the thousands of laboratory studies on EMF could build a case for nearly any health endpoint epidemiologists might choose to study.

Any decision rule about what questions are worthy of publication incurs errors. The main costs of erring on the side of publishing research that addresses minimally justified questions are the opportunity costs for the other papers not published and the promulgation of misleading information that encourages pursuit of unpromising pathways. On the other side, failure to publish on topics because the knowledge base is limited may preclude us from opening up important new research avenues. One has to start somewhere, and research that moves from no evidence to modest evidence has value, just as does research that moves from virtual to utter certainty.

For topics that have an epidemiologic literature in place, the new study must make a contribution to refining our understanding of the potential association. For the extensively studied topics, this calls for superiority to the preceding studies in at least some important respect. For topics such as residential EMF and childhood leukemia, and occupational EMF and adult leukemia and brain cancer, that is a daunting task given the volume and quality of research already completed. For other less extensively studied avenues driven by the epidemiologic evidence, such as the association of EMF with amyotrophic lateral sclerosis or with miscarriage, the bar is not quite so high. Additional studies at least equal in quality to those that have come before would be contributory, but the endpoints themselves are challenging ones for epidemiologic inquiry. Unless the empiric (not just the theoretic) support for hypothesized biological mechanisms of EMF effects becomes much more convincing, 15 it will be difficult to motivate epidemiologic studies based primarily on theoretic mechanisms alone.

Policy applications and public concern remain a valid justification for environmental epidemiology in general and research on EMF in particular, but if that is the primary motivation for research, a compelling case for immediate policy relevance needs to be made. The recent work on cellular telephones and brain cancer is readily justified by specific public concerns, whereas examination of potential effects of EMF on birth defects, for example, would be hard to defend on those grounds. At present, a potential association of EMF and birth defects is not a primary consideration for policy makers. Although a formal decision-rule on what topics are and are not of interest cannot be articulated, the burden is on the authors to make a case that their question is worth asking. Outstanding rigor in design, execution and analysis does not compensate for a weakly justified research question. If it is not worth doing, it is not worth doing well.

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About the Author

DAVID SAVITZ conducted one of the early studies of exposure from power lines near residences in Denver, Colorado, in the early 1980s, and a study of electric utility workers in the United States that was initially released in 1995. He has served on a number of review groups, including a panel of the National Research Council that he co-chaired. He is Chair of the Department of Epidemiology at the University of North Carolina School of Public Health.

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© 2003 Lippincott Williams & Wilkins, Inc.