Comments on "PM2.5 and Mortality in Long-term Prospective Cohort Studies: Cause-Effect or Statistical Associations?"
The lengthy commentary by Gamble (1) is rife with inaccuracies, all of which cannot be commented on in the context of this reply. However, because Gamble's critique largely is directed toward ecological studies, we wish to focus on a number of widespread misconceptions to which his critique has succumbed. We have discussed these issues at length in a recent publication in EHP (2). Contrary to his assertion, none of the major studies (cohort, times-series or cross-sectional) cited and criticized by Gamble truly are ecological studies. Having incorrectly categorized the studies, he then proceeded to cite commentaries (3,4) that point out the significant limitations of ecological studies when the target of inference is individual risk.
The hallmark of ecological studies is the lack of individual-level measurements. Thus, the ecological study merely relies on a comparison of aggregate (group)-level prevalence or incidences of outcomes with some aggregate level of exposure. For example, in a paper cited by Gamble, Brenner et al. (3) used county-specific mortality rates for lung cancer and estimates of the prevalence of smoking for each county to demonstrate the pitfalls of the use of group data to make inferences about individual risk. The cohort and several of the large multicenter cross-sectional studies cited by Gamble differ from Brenner's example on two crucial points: 1) they contain large sets of individual data (as acknowledged by Gamble), which include most of the relevant risk factors and potential confounders for which adjustment might be necessary; and 2) exposure is not an average proportion of the population that is exposed (as was the case in the Brenner example), but rather a crude average ambient concentration measured in a particular city. It is this second characteristic of what we have called the "semi-individual study design (2) that often leads to the misapplication of the term "ecological" to the study design. Brenner et al. (3) noted that exposure prevalence in a truly ecological study suffers from the fact that the unknown sensitivity and specificity of the exposure assignment has a substantial impact on the potential distortion of the ecological exposure-outcome association relative to the "true" individual-level association. Moreover, prevalence (of smoking, for example), an inherently group-level concept, has no interpretation at the level of the individual. In contrast, in a semi-individual study of the type critiqued by Gamble, the exposure (ambient particle concentration) clearly is of relevance for all individuals who live in a particular region. The ambient levels of particles are not an average between those exposed and unexposed, but rather an estimate of the ambient concentration that applies to all persons. Obviously there will be variability around this estimate, which depends on the exact location of homes and work places, time-activity patterns, use of air conditioners, etc. The distribution of such factors in a population define the level of variability around the central estimate and, indeed, for pollutants with large indoor/outdoor gradients such as ozone, the variability around individual estimates of exposure based on an ambient concentration may be substantial. For fine particles, which have a higher penetration into indoor environments, this variability will be smaller.
In contrast to a true ecological study, the semi-individual studies to which Gamble refers share all of the problems that relate to errors in exposure, i.e., exposure misclassification. Gamble failed to address this issue at all, despite its considerable importance. The critical questions relate to how accurate the ambient concentration is as a surrogate for individual exposure and how the errors in these exposure estimates influence the estimates of the effect of ambient air pollutants on disease morbidity and mortality. In this context, the relationship between the error in exposure and the true exposure and the overall range of exposure across the cities in semi-individual studies are of central concern. Wacholder (5) presented a framework to address the issue of error structures. Other authors have discussed analytical strategies to address these problems in semi-individual studies (6). Gamble seems to be unaware of this work and its relevance to his critique.
Gamble places considerable credibility in the Seventh Day Adventist Study (7), although this study is a prime example of a semi-individual study design. The fact that this study did not show an association between particle exposures and life expectancy, in part, can be attributed to the relatively small sample size and relatively short follow-up times as compared to the Six Cities Study of Dockery et al. (8). The Adventist study did make a concerted attempt to improve the individual exposure estimates by taking into account a number of the factors that can lead to variability of such estimates when they are based solely on a central ambient monitor (7). The approach of these investigators, when combined with a large range of exposures across the study population, may be the most promising strategy to reduce the variability in the exposure estimates (9). We accept that the findings of the Adventist study, with regard to increased air pollution-associated morbidity, is consistent with the coherence criterion (1). However, we have some difficulty in understanding why a population with higher risks for respiratory morbidity should not have reduced life expectancy because chronic respiratory disease and its attendant decrease in lung function are risk factors for increased risk of death (10,11). It is this type of coherence between different health outcomes, both short-term and long-term, which, when taken as a whole, provide the strongest evidence for a causal effect of ambient air pollution and decreased health. Indeed, recent work (12,13) indicates that increased levels of particulate matter are associated with reduced pulmonary function, the latter a strong predictor of mortality (10,11). Seen in this context, lung function may be the link between air pollution and the observed increased mortality. Gamble's reference to lung function as a potential confounder indicates his lack of appreciation for the fact that lung function may be on the causal pathway--a fact that would disqualify it from being considered as a confounder (14).
It appears that Gamble has applied to the issue of the public health implications of air pollution the same strategies used successfully by the tobacco industry to obscure the public debate on the health consequences of cigarette smoking--offering pseudoscientific critique to cloud the debate. What is required instead is a clearer explanation to the public of the strengths and limitations of various approaches to the study of this problem and an ongoing effort by epidemiologists and environmental scientists to improve the quality of the studies that are to be performed in the future. It appears that Gamble and his company had rather content themselves with clouding rather than clarifying the complex problem of the interface between science and regulation.
Nino Künzli
Institute for Social and Preventive Medicine
University of Basel,
Basel, Switzerland
Ira B. Tager
Division of Public Health Biology and Epidemiology
School of Public Health
University of California, Berkeley
Berkeley, California
References and Notes
1. Gamble J. PM2.5 and mortality in long-term prospective cohort studies: cause-effect or statistical associations? Environ Health Perspect 106:535-549 (1998).
2. Künzli N, Tager I. The semi-individual study in air pollution epidemiology: a valid design as compared to ecologic studies. Environ Health Perspect 105:1078-1083 (1997).
3. Brenner H, Savitz D, Joeckel K, Greenland S. Effects of nondifferential exposure misclassification in ecologic studies. Am J Epidemiol 135(1):85-95 (1992).
4. Greenland S. Divergent biases in ecologic and individual-level studies. Stat Med 11:1209-1223 (1992).
5. Wacholder S. When measurement errors correlate with truth: surprising effects of nondifferential misclassification. Epidemiology 6(2):157-161 (1995).
6. Navidi W, Thomas D, Stram D, Peters J. Design and analysis of multilevel analytic studies with applications to a study of air pollution. Environ Health Perspect 102(suppl 8):25-32 (1994).
7. Abbey D, Moore J, Petersen F, Beeson L. Estimating cumulative ambient concentrations of air pollutants: description and precision of methods used for an epidemiologic study. Arch Environ Health 46(5):281-287 (1991).
8. Dockery D, Pope A, Xu X, Spengler J, Wae J, Fay M, Ferris BJ, Speizer F. An association between air pollution and mortality in six U.S.Cities. N Engl J Med 329(24):1753-1759 (1993).
9. Künzli N, Lurman F, Segal M, Ngo L, Balmes J, Tager I. Association between lifetime ambient ozone exposure and pulmonary function in college freshman--results of a pilot study. Env Research 72(1):8-23 (1997).
10. Ashley F, Kannel W, Sorlie P, Masson R. Pulmonary function: relation to aging, cigarette habit, and mortality; the Framingham Study. Ann Internal Med 82:739-745 (1975).
11. Neas LM, Schwartz J. Pulmonary function levels as predictors of mortality in a national sample of US adults. Am J Epidemiol 147(11):1011-1018 (1998).
12. Ackermann-Liebrich U, Leuenberger P, Schwartz J, Schindler C, Monn C, Bolognini G, Bongard J, Brändli O, Domenighetti G, Elsasser S, et al. Lung function and long-term exposure to air pollutants in Switzerland. Am J Respir Crit Care Med 155(1):122-129 (1997).
13. Neas L, Hoek G, Dockery D. Air pollution and the incidence of adult pulmonary function deficits in six US cities [abstract]. Epidemiology 9(4):S160 (1998).
14. Rothman KJ. Modern Epidemiology. Boston/
Toronto:Little, Brown and Company, 1986.
Reply to Kunzli and Tager Regarding Causality in PM2.5 Cohort Studies
Kunzli and Tager suggest that my critique (1) of PM2.5 and mortality in long-term prospective cohort studies is full of inaccuracies and misconceptions about ecological studies. As in most arguments, there are issues on which there is agreement, others where there is disagreement, and some areas of misunderstanding. I will briefly discuss those relevant issues on which we disagree. I believe that the cohort studies are accurately described, that the ambient PM2.5 concentrations are inadequate surrogates for individual-level exposure, and that these studies are subject to some biases and inaccuracies common to true ecological studies. In my paper (1), I suggested that risk estimates based on ambient concentration levels should be tested for plausibility using other studies with both individual-level exposure and response data, and I applied such a test. I presented evidence that short-term exposures in time-series studies are not coherent with long-term health effects and that long-term morbidity findings may not be
coherent with mortality. I suggested that the Six Cities results might be confounded, using between-city differences in lung function as one example.
I did not present the air pollution studies as being truly ecological. In my paper (1), I described the cohort studies as "a mixed design incorporating both individual-level data...and group-level data on ambient air pollution concentrations." More precise terms such as semiecological, or hybrid, or semi-individual may be helpful. In my opinion, a lack of consideration for the limitations inherent in ecological exposure variables has led to significant errors in interpretation.
Kunzli and Tager appear to suggest that the pollution exposure variable is not ecological because it is derived from measurement (i.e., it is a "crude, average ambient concentration"). It is true that Brenner et al (2) state that in "ecologic studies, the exposure status of groups is often defined by the proportion of individuals exposed." Kunzli and Tager apparently missed the word "often" or interpreted it as "always." Brenner et al (2) go on to indicate that exposure characterized by a single common measure such as "area air pollution" is an ecologic exposure variable.
We seem to agree that there are errors in using ambient concentrations as surrogate measures for individual exposure, that these errors influence the risk estimates, and that these are critical questions. We appear to disagree on how great is the effect, how to estimate the effect of these errors, and whether I have addressed the issues at all.
I discussed exposure misclassification, and I concluded that since all inhabitants in a given city are assumed to have the same exposure to PM2.5, there are large errors for many members of the cohorts (1). Therefore, the group-level exposure variable is not an adequate surrogate for personal exposure, and as a result, the risk estimates may be biased to an unknown extent and direction. The magnitude and direction of this misclassification bias cannot be easily estimated because it has been repeatedly shown that even apparently nondifferential misclassification can cause spurious results in either direction (3-8). In fact, when the true relative risk is near 1.00 (as is the case for PM), an appreciable percentage of studies will over-estimate the risk (9). When the true relative risk is exactly 1.00, the misclassified risk estimates are evenly distributed above and below 1.00 (8). While exposure misclassification may be reduced by the use of such individual-level data as time-activity patterns or work exposure [as in the studies of the Seventh Day Adventists (SDAs) (10)], the potential for error still remains.
It is true that semiecological studies gather some covariate estimates for individuals, providing some control of confounding. However, considerable residual confounding can still occur if important confounders are missed or crudely measured (5,11-15). Furthermore, for individual-level confounding to be effectively removed, the nature of the association between the exposure and the confounder should be well specified, which is not possible when exposure information for individuals is lacking.
Some questions regarding the inaccuracies associated with the risk estimates from these studies may be addressed in ways suggested by Kunzli and Tager. I go beyond these suggestions to propose that the ultimate validity of the risk estimates in these studies is basically unknown. The risk estimates must be verified or refuted by a different study design utilizing individual-level data for exposure, outcome, and confounding variables (1).
This process of verification or refutation is an essential part of the scientific method in general and epidemiology in particular (16). A primary focus of my critique was to verify and refute the mortality risk estimates from the Six Cities (17) and American Cancer Society (ACS) (18) cohorts. This validity check was done by comparing the cardiopulmonary mortality risk estimates for ambient PM2.5 with the risk estimates for tobacco smoke in these same studies. The rationale for this comparison was that the individual-level exposure to tobacco smoke PM was well characterized, that the associations between tobacco smoke and cardiopulmonary mortality are widely accepted as causal, and that tobacco smoke PM is a reasonable surrogate for ambient PM2.5. The comparability of the ambient PM2.5 and tobacco smoke risk estimates would be a validity check and would provide some estimate of the degree and direction of bias if the results were not comparable. For a given PM2.5 concentration, the risk estimates from ambient exposures were orders of magnitude greater than those from tobacco exposures. Therefore, I concluded that the ambient PM2.5 risk estimates in the Six Cities (17) and ACS (18) cohort studies are not biologically plausible (1).
I and others (17,19) disagree with Kunzli and Tager that short-term mortality in time-series studies is relevant to the coherence argument because the time-series studies look at short-term exposures rather than chronic or lifetime exposures. Also, the health outcomes in time-series studies are usually thought to be in the elderly and other susceptible people (20) rather than in the total population.
It is unclear whether the SDA long-term morbidity results (10) are coherent with mortality results. Among individuals who were symptom-free at the start of the study, there was an association between increased symptoms and PM. These risk estimates were 40-fold greater than those estimated for smoking. There were no analyses presented for those individuals who had symptoms at the start of the study, but became symptom-free at the end of the study. This analysis is just as important as the analysis of incidence of new symptoms. If both showed an association with PM, the results would not be internally coherent (1).
I presented evidence showing why reduced lung function could be a confounder in these studies and that it meets the criteria for confounding.First, reduced lung function must be a risk factor for increased mortality (1). Second, reduced lung function must be correlated with between-city variations in PM2.5, although the relationship shown in Figure 3 (1) could only be tested with the ecologically based exposure measures used in that study. Third, reduced lung function should not be on the same causal pathway as PM2.5 for mortality; the point of the example shown in Figure 4 (1) was to suggest that important differences occur in the distribution of risk factors between cities, with lung function being one of many possible risk factors. I do not believe that adjustment for a few individual-level risk factors has adequately addressed the complex overall potential for confounding in these studies. We all realize that we can never make all groups completely comparable, but between-city differences in PM2.5 concentrations are so small and relative risks so low that these studies are particularly susceptible to even slightly confounded results.
I believe this paper(1) and the questions raised by Kunzli and Tager are in line with the scientific process of verification and refutation. They have led to further discussion that will hopefully lead to additional testing. However, it is disappointing that Kunzli and Tager chose to question the integrity of the author's motivation based on affiliation. Judgement on whether or not my critique clouds the complex issues around PM2.5 and mortality should be determined not by my affiliation but solely on the scientific merits of the argument.
I thank John Bukowski, Wendy Huebner, Mark Nicolich, and Rob Schnatter for their stimulating discussions and input.
John Gamble
Exxon Biomedical Sciences, Inc
East Millstone, New Jersey
References and Notes
1. Gamble JF. PM2.5 and mortality in long-term prospective cohort studies: cause-effect or statistical associations? Environ Health Perspect 106:535-549 (1998).
2. Brenner H, Savitz DA, Jockel K-H, Greenland S. Effects of nondifferential exposure misclassification in ecologic studies. Am J Epidemiol 135:85-95 (1992).
3. Birkett NJ. Effect of nondifferential misclassification on estimates of odds ratios with multiple levels of exposure, Am J Epidemiol 136:356-362 (1992).
4. Flegal KM, Keyl PM, Nieto FJ. Differential misclassification arising from nondifferential errors in exposure measurement. Am J Epiddemiol 134:1233-1244 (1991).
5. Flegal K. More on the mismeasurement of exposure issue. Epidemiol Monit 17:5-6 (1996).
6. Dosemeci M, Wacholder S, Lubin JH. Does nondifferential misclassification of exposure always bias a true effect toward the null value? Am J Epidemiol 132:746-748 (1990).
7. Wacholder S. When measurement errors correlate with truth: surprising effects of nondifferential misclassification. Epidemiology 6:157-161 (1995).
8. Thomas DC. Re: "When will nondifferential misclassification of an exposure preserve the direction of a trend?" [letter]. Am J Epidemiol 142:782-783 (1995).
9. Sorahan T, Gilthorpe MS. Non-differential misclassification of exposure always leads to an underestimate of risk: an incorrect conclusion. Occup Environ Med 51:839-840 (1994).
10. Abbey DE, Lebowitz MD, Mills PK, Petersen FF, Beeson WL, Burchette RJ. Long-term ambient concentrations of PM10 and development of respiratory symptoms in a nonsmoking population. Arch Environ Health 50:139-152 (1995).
11. Weinberg CR, Umbach DM, Greenland S, Weinberg et al. reply [letter]. Am J Epidemiol 142:784 (1995).
12. Brenner H. Bias due to non-differential misclassification of polytomous confounders. J Clin Epidemiol 46:57-63 (1993).
13. Brenner H. A potential pitfall in control of covariates in epidemiologic studies. Epidemiology 9:68-71 (1997).
14. Marshall JR, Hastrup JL. Mismeasurement and the resonance of strong confounders: uncorrelated errors. Am J Epidemiol 143:1069-1078 (1996).
15. Savitz DA, Baron AE. Estimating and correcting for confounder misclassification. Am J Epidemiol 129:1062-1070 (1989).
16. Rothman KJ, ed. Causal Inference. Chestnut Hill, MA:Epidemiology Resources, Inc, 1988.
17. Dockery DW, Pope CA III, Xu X, Spengler JD, Ware JH, Fay ME, Ferris BG Jr, Speizer FE. An association between air pollution and mortality in six U.S. cities. N Engl J Med 329:1753-1759 (1993).
18. Pope CA, Thus MJ, Namboodiri MM, Dockery DW, Evans JS, Speizer FE, Heath CW Jr. Particulate air pollution as a predictor of mortality in a prospective study of U.S. adults. Am J Respir Crit Care Med 151:669-674 (1995).
19. McMichael AJ, Anderson HR, Brunekreef B. Cohen AJ. Inappropriate use of daily mortality analyses to estimate longer-term mortality effects of air pollution. Int Epidemiol Assoc 27:450-453 (1998).
20. Utell JM, Frampton MW. Particles and mortality: a clinical perspective. Inhal Toxicol 7:645-655 (1995).
Methylmercury Neurotoxicity Independent of PCB Exposure
A prospective study of methylmercury neurotoxicity in a Faroese birth cohort (1) has been scrutinized at a workshop recently summarized in EHP (2). The meeting was convened by the NIEHS on behalf of the White House Office of Science and Technology Policy. One of the main issues considered by the expert panels was whether concomitant prenatal exposure to polychlorinated biphenyls (PCBs) affected the neurobehavioral response variables assessed at 7 years of age. In a previously published paper (1), we showed that adjustment for the cord PCB concentration barely changed the regression coefficients for the cord-blood mercury concentration as a predictor of neurobehavioral deficits. In response to questions raised at the workshop, we have now conducted some additional analyses to explore this issue
On the basis of the 436 cord PCB analyses completed (1), children with complete data were divided into tertile PCB exposure groups. The main source of increased PCB exposure in the Faroe Islands is whale blubber, but almost half of Faroese mothers are known not to eat this food item (3). The lowest tertile is therefore thought to correspond to a control group with a background exposure to PCB. Based on psychometric properties, one outcome variable was selected to reflect each of five different domains of brain function, i.e., motor function, attention, visuospatial function, language, and memory (1). A regression equation with a uniform series of confounder variables (1) was then fitted to the data for each of the three subgroups.
Table 1 shows the regression coefficients for the logarithmic transformation of the cord-blood mercury concentration, i.e., the change in the outcome variable associated with a 10-fold increase in methylmercury exposure. The hypothesis of no difference between the regression coefficients was then tested, and in all cases resulted in an acceptance of the hypothesis, with p-values of 0.16-0.94. Accordingly, the effect of mercury exposure can be explained by three parallel lines. The hypothesis of no PCB effect resulted in p-values between 0.07 and 0.73, thus suggesting no difference in the intercept between the three lines. Thus, given the acceptance of both null hypotheses, the effect of mercury exposure on each of the five neurobehavioral outcome variables can be explained by a single line. All mercury regression coefficients for the control group suggest a deficit at increasing concentrations similar to the one for the overall material (1). Also, when compared to the two other tertile groups, the mercury effect in the control group was the greatest for three of five outcome variables
However, some information may be lost, as the PCB exposure variable in this analysis was reduced to tertile classes only. Thus, the possible effect modification by PCB exposure was investigated in regression analyses, which in addition to the confounders, also included the mercury and PCB exposure variables as well as a product term between the two exposure biomarkers. The p-value for no effect modification was between 0.21 and 0.75, thus suggesting that no interaction occurred. As previously reported (1), an independent effect of PCB exposure was suggested for the Boston Naming Test, although it affected the mercury regression coefficient only slightly
All of the above calculations were based on the wet-weight PCB concentrations, which showed a better correlation (r = 0.41, after logarithmic transformation) with the cord-blood mercury concentration than did the lipid-based PCB concentration (r = 0.31). The potential confounding and interaction effect were thereby maximized. No significant relationship with the outcome variables was found when using the lipid-based cord concentration as the PCB exposure biomarker. However, both PCB and methylmercury exposure biomarkers are likely to be imprecise indicators of the causative neurotoxicant concentrations, thereby possibly resulting in attenuated regression coefficients. Nonetheless, among the exposure biomarkers examined, the cord-blood mercury concentration remains the best predictor for neurobehavioral dysfunction in this population (1). The expanded analyses do not suggest that the mercury effect can be explained by concomitant PCB exposure or that PCB exposure results in an increased mercury-associated effect.
Esben Budtz-Jørgensen
Niels Keiding
Department of Biostatistics
Panum Institute
University of Copenhagen,
Copenhagen, Denmark
Philippe Grandjean
Roberta F. White
Institute of Public Health
Odense University
Odense, Denmark
and Departments of Neurology and Environmental Health
Boston University Schools of Medicine and Public Health Boston, Massachusetts
Pál Weihe
Department of Occupational and Public Health
Faroese Hospital System
Tórshavn, Faroe Islands
References and Notes
1. Grandjean P, Weihe P, White RF, Debes F, Araki S, Murata K, Sørensen N, Dahl D, Yokoyama K, Jørgensen PJ. Cognitive deficit in 7-year-old children with prenatal exposure to methylmercury. Neurotoxicol Teratol 19: 417-428 (1997).
2. Forum: Meeting of the minds in mercury. Environ Health Perspect 107:A12 (1999).
3. Steuerwald U, Weihe P, Jørgensen PJ, Bjerve K, Brock J, Heinzow B, Budtz-Jørgensen E, Grandjean P, unpublished data.
Last Updated: April 15, 1999