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Commentary: Response to Environmental PollutionMore Research May Not Be Needed

Savitz, David A.

doi: 10.1097/EDE.0000000000000526
From the ISEE

From the Departments of Epidemiology and Obstetrics and Gynecology, Brown University, Providence, RI.

The author reports no conflicts of interest.

Correspondence: David A. Savitz, Departments of Epidemiology and Obstetrics and Gynecology, Brown University, 47 George Street, 3rd Floor, Providence, RI 02912. E-mail:

The scenario has become all too familiar to environmental epidemiologists and the public: a population is discovered to have been exposed to a hazardous pollutant and there is a well-justified public outcry for an appropriate response to the episode, often including the call for epidemiologic research to determine whether the exposure in question has indeed caused public health harm. Unlike the other components of a response, such as ensuring that the exposure ceases, determining the cause so that future episodes can be prevented, providing health care to those in need, or seeking to punish the guilty, an epidemiologic study seldom offers direct benefit to those affected and studied, and actually has the potential for causing inadvertent harm. The risks and benefits of embarking on an etiologic study in response to such events need to be examined carefully to ensure that what is possible is in fact useful. Too often, the claim that “we need to do an epidemiologic study” is given insufficient scrutiny, as though a failure to do so somehow reflects a lack of concern for those at risk. Or more cynically, it can be used to buy time and avoid actions that would have direct benefit.

Those who were exposed, often represented by community activists, political leaders, or attorneys with an interest, seek research that will provide proof of the harm that they believe has resulted from this exposure. Public health agencies want to be responsive to their constituents and may believe that providing scientific evidence of the exposure–disease association of concern in the affected population is a necessary part of the response. Those who are responsible for the exposure may seek research to support their belief that the exposure has resulted in little or no health harm. And of course, environmental epidemiologists seek the opportunity to do environmental epidemiology—to show how useful our skills are in addressing the problem and supporting the affected community. Unfortunately, what often follows is a lengthy and contentious process of developing research plans (always slower than expected or desired), recognition of serious limitations in the quality of research that is feasible due to inadequate exposure or health data or small populations, disappointment when the results do not allow for unambiguous conclusions, followed by arguments among the advocates, public health agencies, and polluters over what the findings mean. Sometimes, the cycle repeats with a “new and better study” plan, now even more prolonged, expensive, and often no more definitive than the first. This scenario of despair suggests that those of us who practice environmental epidemiology must think carefully before presuming that our skills are always those needed to address a problem.

Before embarking on a study, whether motivated by scientific curiosity, a local controversy, or a request by community members or a public health agency, we need to ask at the outset “to what end?” If the purpose of the study is to advance basic scientific knowledge regarding the presence of an etiologic relationship between exposure and disease, all the usual criteria for assessing the merits of a study should apply—the current state of knowledge, whether the population is large enough for informative study, whether the information that can be obtained on exposure, outcome, and potential confounders is adequate to advance the field, etc. In many cases of discrete pollution episodes, the quality of the exposure information or the study size are not favorable for advancing our basic understanding of the etiologic relationship of interest. Sometimes, such research opportunities do arise from disasters, as demonstrated by the research on dioxin and cancer from the Seveso, Italy contamination1 and on polychlorinated biphenyls and neurodevelopmental disorders resulting from the rice poisoning episode in Kyushu, Japan.2

If the primary goal of additional research is not to produce new fundamental knowledge of the etiologic relationship but instead to quantify the adverse health effects of exposure in this specific population, the proposed study has to be of a quality that the results will be scientifically defensible regardless of how they come out. Research intended to “show how harmful it was” or “show that no harm was done” or to “show people how much we care” is of questionable benefit and potentially harmful because by definition, epidemiologic research generates unpredictable results. Are we prepared to accept that a null study in which no relationship between exposure and outcome is identified as providing evidence that health was not harmed in this particular situation? Would positive evidence consistent with the presence of an etiologic relationship provides direct, credible indications that some fraction of individuals in this population suffered disease due to the exposure? Only if both these questions can be answered affirmatively can a case be made that etiologic research applicable to the local population is valuable.

What harm can result from conducting environmental epidemiology studies in response to pollution episodes? First, there is often a delay in taking the other needed actions while awaiting the results of the study, which often take years to complete. Second, the results are highly susceptible to misinterpretation or over-interpretation as the “bottom line” despite what are often severe methodologic limitations. Third, such studies often perpetuate the controversy and anxiety in the community, plaguing the community with the reverberating message that “we just don’t know.” Holding out for clear responses to unanswerable questions can distract the public health community and citizens from fully grasping and using the solid information that is already available—who was exposed, how much were they exposed, what do we know from previous research on the potential health effects of that exposure? Rather than research aimed at providing precise information on causal relationships, a targeted effort to characterize exposure as fully and rapidly as possible would be more feasible and valuable.

For example, in the case of the recent concern with lead contamination of the drinking water supply in Flint, Michigan,3 there is already extensive knowledge about the effects of lead exposure on child development, and the potential for discerning health consequences within the local population has no bearing on any of the key actions that should follow: determine the origins of the problem and responsibility for the contamination, take action to prevent future episodes, and provide screening, counseling, and assistance to those who are rightly concerned about their child’s well-being. Rather than conducting a lengthy new epidemiologic study that is likely to be of limited quality, public health might be better served by promptly providing clear information to those affected by the exposure on what we do know and access to health services, and as appropriate, holding those responsible fully accountable. Affected communities would be best served by focusing on these practical, resolvable concerns and not on the likely unanswerable question of whether a given individual or even whether some fraction of the population directly suffered health harm as a result of exposure.

One form of applied research can be of great value in such circumstances: health impact assessment. If the exposure circumstances can be estimated with reasonable accuracy, ideally with information on the increment in exposure due to the episode relative to baseline levels, then a far better estimate of the health impact would be generated by applying current scientific knowledge of exposure–disease relationships than by conducting a new study in the population of interest. While it could be argued that unique attributes of this population make application of the standard risk estimates questionable, it is very unlikely that a study with sufficient precision can be done in the affected population to demonstrate such effect modification. In contrast to protracted, expensive, and disappointing etiologic research, credible risk estimates should be attainable within weeks or a few months of the episode. A quick and dirty estimate of health consequences of this nature is likely to have a more favorable cost–benefit balance than a more ambitious, often futile, new epidemiologic study.

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1. Pesatori AC, Consonni D, Bachetti S, et al. Short- and long-term morbidity and mortality in the population exposed to dioxin after the “Seveso accident”. Ind Health. 2003;41:127–138.
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