Weisskopf, Marc G.
From the Departments of Environmental Health and Epidemiology, Harvard School of Public Health, Boston, MA.
Editors’ note: This series addresses topics of interest to epidemiologists across a range of specialties. Commentaries start as invited talks at symposia organized by the Editors. This paper was presented at the Third North American Congress of Epidemiology held in Montreal in June 2011.
Editors’ note: Related articles appear on pages 785, 790, and 795.
The author reports no conflict of interest.
Correspondence: Marc G. Weisskopf, Department of Environmental Health/EOME, Harvard School of Public Health, Landmark Center, 401 Park Dr. PO Box 15697, Boston, MA 02215. E-mail: email@example.com.
There is growing interest in environmental health about potential neurologic effects of air pollution.1–4 Let us consider for the moment the issue of cognitive function in adults: how can we best address the question of whether air pollution causes impairment in cognitive function? For simplicity, let us consider PM2.5 (particulate matter of <2.5 µm diameter) as our air pollutant of interest. We might ask whether exposure to a given level of PM2.5 for, say, 5 years among, say, a group of adults older than 50 years at the start would lead to a decrease in cognitive function. From a causal perspective, we would ideally assemble a group of 50-year olds, assess their cognitive function at baseline, outfit them all with a personal breathing apparatus, randomly assign half to breathe air with a given level of PM2.5 for 5 years while the other half got air free of PM2.5, then test their cognitive function at the end, and compare the change in cognitive function of those who breathed the more polluted air with those who breathed clean air. For many ethical and practical reasons, this approach is obviously not possible. So, what is an environmental epidemiologist to do?
In general, we usually do not associate randomized trials with environmental epidemiology. However, there are some situations in which this may be possible—although the form of these trials would be a little different from randomized trials in other settings. Specifically, rather than exposing subjects to something, we may be able to provide means to reduce exposure. For example, we could randomize cooking stoves that reduce indoor PM2.5 exposure. In theory, if we had complete concordance between assigned and actual treatment, such an approach would allow us to determine the causal effects of using an improved stove to reduce PM2.5 exposure by a specific amount for a given time period. Indeed, this is precisely what we want to know if our aim is to use our stove technology in an intervention to reduce the burden of the health effect in question. Of course, this estimate of effect is not necessarily the causal effect of reducing PM2.5 exposure. For example, a new stove might change cooking patterns and thus eating patterns, which in turn could possibly affect cognitive function. If we wanted to know the causal effect of the reduction in PM2.5 itself, rather than the causal effect of introducing a new stove, we would need to restrict any changes in eating habits (and any other unintended consequences of the new stove) in the two arms of the study. Perhaps, cooking times shorten so that people spend more time exercising outside—that would have to stop! Controlling for other possible paths to cognitive function that result from our stove intervention, of course, gets more difficult the more possible alternate paths there are. But at least by knowing what the intervention is—new stoves—we can hope to identify those other paths.
One problem with randomized trials in environmental epidemiology, like the stove intervention, is that such trials are usually performed in high-exposure settings to maximize changes in the exposure. This runs the risk of null results, not because less exposure to PM2.5 has no effect on cognitive function, but because the damage to cognitive function (or any other health outcome) in high-exposure settings may already be maximally affected by longstanding exposure to PM2.5. Although this would be the correct causal answer to our stove intervention, the answer may have been different if we had exposed people to PM2.5 rather than removed a longstanding exposure to PM2.5.
Another problem with trials is that for PM2.5, and many other toxicants that might be amenable to similar interventions, there are many known adverse health effects of excessive exposure. Therefore, even though a randomized trial of exposure reduction would avoid the obviously unethical approach of deliberately exposing some subjects to toxicants, it remains somewhat ethically questionable to deny some study subjects an intervention that is known to reduce exposure—particularly in a setting where exposures are routinely high. In practice, the randomization can still be done to some degree, for example, by taking advantage of phased rollout of new devices and randomizing subjects to receive the intervention early or late in the rollout. However, this more often would involve differences on the order of months in the timing of receiving an intervention, rather than a period as long as 5 years. A causal question targeted at a short period of exposure may be more feasible, but many effects may simply not occur or be too small to detect in that time frame, even if detectable with longer exposure.
Outside of these possibilities, the environmental epidemiologist is usually stuck with observational study designs and all their inherent difficulties. A common approach for studies of air pollution is to either use central outdoor ambient air monitors to assign exposures to everyone in some region around that monitor or build models of ambient air pollution levels based on those monitors and other predictors of air pollution levels such as traffic patterns and meteorologic conditions. These approaches have the obvious drawback of introducing measurement error, although we generally expect that error to be nondifferential with respect to outcomes. However, they have the advantage of more easily estimating exposures for large numbers of people than, say, outfitting study participants with personal breathing space monitors. In fact, if we are thinking of policies or other interventions to reduce exposure to air pollutants, we are usually considering actions to reduce ambient air pollution levels.
What if we were to consider a policy of higher gas taxes to discourage driving and so reducing traffic-related PM2.5 exposure? How could we study whether that will have the effect of improving cognitive function? We could imagine a trial where people are randomized to a land of higher gas taxes or one of the status quo. This trial may show a wonderful reduction in PM2.5 and improvement in cognitive function of the people randomized to the land of higher gas taxes. However, it might also turn out that the people in the land of higher gas taxes started walking more, which might also have an effect on cognitive function. This may even be another beneficial effect of our intervention, so we are happy! However, what happens if the automobile lobby takes our results and says that the beneficial effects of raising gas taxes on cognitive function was in fact the result of increased walking, rather than reduced PM2.5? They then argue that we should be setting policies to increase walking rather than increase gas taxes. So, we would have to redo our intervention study and this time force everyone to walk the same amount in both lands to get only the effect of raising gas taxes that occurs as a result of reduced PM2.5.
In the observational study setting, this would translate in directed acyclic graph terminology to trying to block the backdoor path5 from reduced PM2.5 exposure to cognitive function through walking. We can do this by conditioning on any variable that is on the path from PM2.5 to cognitive function that passes back from PM2.5 (rather than out from it) to cognitive function and goes through walking, eg, walking itself. However, if we truly want to know the causal effect of reduced PM2.5 exposure, we need to block all possible backdoor paths from reduced PM2.5 exposure to cognitive function. For example, people in town A may have lower PM2.5 exposure than people in town B because the factory shutdown in town A but not in town B. But the people in town A may have lost income because of the factory closing, so now the diet is worse than in town B, many develop diabetes, and as a result, these residents have worse cognitive function. Although these possible backdoor paths can be difficult to identify and block, we can imagine causes of differences in PM2.5 exposure and explore them in causal analyses.6 This is usually true of environmental exposures in general.
An additional advantage with studies of air pollution compared with many other exposures is that the world of possible common causes of air pollution exposure and cognitive function (or any other outcome of interest) is probably more limited—diet, for example, certainly does not cause air pollution exposure, although it might be a common cause of, for example, diabetes and cognitive function. In addition, many factors that drive differences in air pollution do not obviously affect cognitive function (or other health outcomes) by other means, eg, weather patterns.
Furthermore, an important consideration for air pollution or any other environmental toxicant is the fact that environmental exposures are external to the individual.6 Unlike, for example, obesity,7 changing the exposure does not by definition mean changing something within the individual. Changes within individuals make it even more difficult to identify effects of the exposure of interest.6,7
In principle, then we should be able to estimate the causal effect of differences in PM2.5 on cognitive function. In general, similar arguments would hold for other environmental toxicant exposures and health outcomes. This is not to say this is an easy task, and there will almost always be some level of concern about the degree to which the environmental epidemiologist has successfully blocked all backdoor paths. How can we support a claim of causality in the face of this? One thing is to see whether associations are consistent across study settings. The backdoor paths we fail to block completely are likely to differ from one study to the next. If results are reasonably consistent across studies, this suggests there is really something causal going on with the exposure itself. Another consideration is evident from in vitro and animal experiments. These can be tightly controlled and provide strong biologic plausibility for causal effects. The drawbacks in terms of human causality, of course, are that they are not studies of humans. Questions will continue as to whether the dose reflects the human experience (in terms of both levels and timing), or whether species differences compromise extrapolation to humans.
There are situations where policy requires a decision: what is an appropriate concentration limit for lead in the air to protect human health? Should bisphenol A be used in infants’ baby bottles? Epidemiologic studies, for all their faults, are still likely to provide some of the best evidence to address these questions, even if inferring causality remains an inexact science. Will we look at imperfect causal evidence with a cavalier eye, as Alfred E. Neumann might, and say “What, me worry?” or will we take a more precautionary perspective? Perhaps, in our gas tax example, we should turn the tables on those autoindustry lobbyists by saying that an effect is there—and until they can prove that it is because of walking and not the air pollutants, air pollution restrictions should remain in place.
I gratefully acknowledge critical comments on versions of this article by Melinda Power and Jennifer Weuve.
ABOUT THE AUTHOR
Marc Weisskopf is an Associate Professor of Environmental Health and Epidemiology at the Harvard School of Public Health. His research focuses on neurological disorders with a particular focus on the influence of environmental contaminants.
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