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and sedentary lifestyle. These factors are often related to one another and to other characteristics that could be associated with heart disease risk. Thus. anv state-of-the-art assessment of risk of heart disease associated with exposure to environmental tobacco smoke should consider and adjust for most, if not all, of these factors in statistical analysis in order to exclude alternative explanations for any associations found. As an extension of my review of the epidemiologic studies of cardiovascular disease and exposure to environmental tobacco smoke presented in my oral testimony at the OSHA hearings (November 1994), I have undertaken a more in-depth assessment of the quality of the studies. In any epidemiologic study, there are several important criteria by which one can independently judge study reliability. These primarily relate to study bias and confounding and chance occurrence. In an effort to critically evaluate these studies according to a standardized list of criteria, I developed a rating sheet that includes the major criteria for study reliability as well as questions whose answers allow determination of whether each of the criteria are iulfilled for a particular study (Appendix A). Detailed summanes of each of the 15 available studies (16 ` papers) on cardiovascular disease and environmental tobacco smoke available to Dr. Brown at the time of his report are provided in Appendix B. Table 1 summarizes my ratings of the quality of each available study according to the rating sheet evaluations found in Appendix A. The criteria on the rating sheets used to create Table I are as follows: 1 Statistically sienificant elevated risks? D or YES Adjusted relative risk (or crude, if adjusted not available) was statistically significant by two-sided test, p<0.05 O or NO Crude or adjusted risk not elevated or risk was not statistically significant by two- sided sided test, p<0.115 O or BLANK No tests or confidence intervals presented for elevated risks. Z Major confoundine considered? • or YES Adjustment for age and gender as well as 4 of the 5 listed risk factors or study ascertained which of the listed risk factors were important and appropriately controlled for them. O or NO No control for age and gender and at least 4 of the 5 risk factors and study did not ascertain important risk factors and appropriately control for them. '-J or BLANK Study did not fully specify what risk factors were controlled for or risk factors unclearly defined (e:g, exercise stress test in the He et al. 1989 study). 16

I I I I I utility for the assessment of workplace PTS effects° (App-2); the findings of the Butler study "are based on too few cases to be reliable" (App-2); the limitations of the Chan study are "sufficient to preclude reliance on the study's data to evaluate the effects of workplace PTS exposure" (App-3); the Kabat and Wynder data "are intriguing, but limitations of the exposure measurements and sample size, in combination with lack of direct control for age or other risk factot•s, undermine their utility". (App-5); and the Lam study's results "lack of specificity and potential for distortion of results by other risk factors are too great for the information to carry much weight" (App-8). Among the cardiovascular studies reviewed by Dr. Brown to assess spousal and workplace environmental tobacco smoke exposure, he comments that the Butler data are "at most suggestive" (A-4); in the Dobson study, ".the potential for bias and confounding leave a causal link with PTS exposure uncertain" (A-9); the Garland study evidence "indicates only a tenuous association" (A-13); the He et a1. (1989) article leaves "room for ambiguity or misunderstanding" (A-18); the Humble study "is more suggestive than conclusive" (A-35); and the Lee study results for ischemic heart disease and stroke are "questionable, particularly so for exposure in all-places from all-sources" (A-44). It is imperative that data be reliable and sufficient enough to reject the null hypothesis of no effect of environmental tobacco smoke exposure. In several instances, Dr. Brown suggests that the data are "consistent" with an effect, but nowhere in his critique does he clearly reject the null hypothesis, nor are the data clearly sufficient to do so. Dr. Brown also acknowledges the absence of adequate exposure assessment data in many of the epidemiologic studies of environmental tobacco smoke. On page 2 of the first deliverable on _ workplace smoking and lung cancer risk, Dr. Brown acknowledges the difficulty in accurately measuring workplace exposure to environmental tobacco smoke, which is a function of the intensity of the exposure due to number of smokers, room size, ventilation, proximity to smokers, etc. For example, in the appendix to this deliverable, he comments that in the Akiba study "it is ... not possible to specify how much of the observed association for work outside the home is due to workplace PTS exposure and how much is due to other occupational exposures" (App-1); in the Buffler study "it is not possible to separate effects attributable to workplace PTS exposure, if any, from those due to other occupational exposures" (App-2); in the Chan study "no differentiation was made betweerr exposure in the home and in the workplace"(App-3); in the Garfinkel study "extremely heavy reliance on proxy respondents ... heightens the potential for exposure misclassification" (App-4); in the Kabat study ". . . only current passive exposure was estimated, rendering the exposure classifications potentially misleading..:'(App-5); and in the Lee study "significant misclassification of relevant exposure is ... a real possibility" (App-9). With regard to lung cancer, Dr. Brown further acknowledges the current absence and need for long-term exposure information due to the lengthy latency period. He states on pages 2 and 3 of the first deliverable on workplace exposure that "efforts at determination of workplace PTS estimates were generally minimal" and that the accuracy of proxy respondents "as sources of workplace PTS exposure estimates is far more questionable." Dr. Brown suggests that the elevated risks associated with employment status outside of the home (or studies in which 3 I

limited number of studies, Dr. Brown does not acknowledge that study results may depend upon the specific disease or death endpoint evaluated. He also does not address the importance of the definition of exposure to ETS in analyzing and comparing study results. For example, some studies are only concerned with current spousal exposure by definition; others combine exposure from spouses of exsmokers and light smokers in the analysis (e:g:, Hirayama). In studies in which risks are elevated (greater than 1.0) in one subgroup only, Dr. Brown makes little attempt to explain such inconsistencies. Examples include male versus female comparisons (Butler et al. 1988, Dobson et al. 1991. Jackson 1989), black versus white (Humble et al. 1990), low socioeconomic status versus high (Humble et al. 1990), and home versus work (Dobson et al. 1991) I I I 1 I I I I I I Improper Use of Statistics There are three fi::.damental problems with Dr. Brown's choice of statistical methodology and the conclusions subsequently derived. These include the incorrect assumption that there is a small probability of so many studies yielding positive results, the inappropriate use of one-tailed statistical analyses, and the reliance on studies with insufficient power to detect relative risks of 1.5. Small Probability of Elevated Risk Occurrence In the first deliverable concerning spousal and/or workplace exposure to environmental tobacco smoke and lung cancer risk, Dr. Brown observes that many studies demonstrate elevated risk '- (i.e., the study results are in the same direction and are of similar magnitude) thereby supporting his conclusion that the association is not due to chance alone. For example, he notes on page 5-43 of the first deli verable on spousal exposure to environmental tobacco smoke that, "li'the points lie more toward the right side of the normal curve than could be likely to occur by chance alone, then the hypothesis of no effect is rejected in favor of a positive association between ETS exposure and lung cancer," and on page 5-52 that "the possibility of chance accounting for the observed associations between ETS and lung cancer has been virtually ruled out by the statistical methods previously applied." - In his conclusions on workplace exposure and lung cancer risk, Dr. Brown comments on page 9 of the first deliverable that, "While few individual studies attain nominal statistical significance, ..., this failing is largely overshadowed by the number of studies observing results in the sstne direction and of similar magnitude (p=0.03 is the probability of 11 or more positive studies out of 14): " It is inappropriate to con^.lude that chance is not a likely explanation for this association on the basis of the probability of positive studies. This exercise is akin to tossing a coin and counting "heads" or ".`tails.° The probability of 11 or more heads out of 14 coin tosses is 0.03. Implicit in this statement, however, is the assumption of a "fair" or unbiased coin, the independence of successive coin tosses, and the assumption that the 14 coin tosses represented a sample of an infinite series of such tosses. Clearly, one cannot equate the 14 datasets on , workplace exposure to envirorunental tobacco smoke with 14 coin tosses. LeVois and Layard 9

Svendsen. K.H., Kuller. L.H.. Martin, M.J.. and Ockene. J.K. 1987. Effects of passive smoking in the Multiple Risk Factor Intervention Trial. Am. J. Epidemiol. 126(5):783-795. Thompson, D.H. and Warburton, D.M. 1993. Dietary and mental health differences between never-smokers living in smoking and non-smoking households. J. Smoking-Related Dis. 4(3):203-211. Woodward. M. and Tavendale, R. 1995. Passive smoking by Tunstall-Pedoe, H., Brown. C.A., self report and serum continine and the prevalence oi respiratory and coronary heart disease,in the Scottish heart helath study. J. Epidemiol. Comm. Health 49:139-143. Tweedie, RL. and Mengersen, K.L. 1995. Meta-analytic approaches to dose-response relationships, with application in studies of lung cancer and exposure to environmental tobacco smoke. Stat. Med. 14:545-559. U.S. Environmental Protection Agency (U.S.EPA). ' 1989. Workshop Report on EPA Guidelines for Carcinogen Risk Assessment: Use of Human Evidence. Office of Research and Development. EPA 625/3-90/017. I !1. i I I I

received considerable attention. Dr. Brown's assessment of dose-response is what Tweedie and Mengersen (1995) referred to as an"unsystematic or 'eve-ball' approach," in that Dr. Brown relies on qualitative comparisons of oddss ratios and occasional reports of statistically significant positive trends in odds ratios in the individual studies alone as evidence of a dose-response. _ _... Tweedie and Mengersen commented that "the use of such qualitative evaluations, without some consideration of the variability in the data, is.liab[e to..lead to misinterpretation." In fact, on page 8 of the first deliverable concerning workplace exposure to environmental tobacco smoke and lung cancer, Dr. Brown acknowledges that the information on dose-response "is too limited in quantity and quality to produce a clear nicture" of any relationship. I I I I 1 ' I I I I have several concerns with Dr. Brown's approach. First, in many of the studies of exposure to environmental tobacco smoke and disease, a trend in odds ratios for different exposure levels is assessed by the investigators or by Dr. Brown using the Mantel extension or other test of linear trend. Such tests, however, do not test the appropriateness of the implicit linear model fitted by these techniques. Modem statistical practice is well described by Breslow and Day (1987) as follows: "When the value of [the goodness of fit statistic] exceeds its degrees of freedom by an amount significantly greater than expected under chi-square sampling, we conclude that the fit is inadequate. Either there are systematic effects that have not been accounted for by the model or else the random variation in disease rates among neighbouring cells is greater than that specified by the Poisson assumption. Agreement between the [goodness of fit statistic] and its degrees of freedom does not guarantee that the fit is good, however, particularly when the degrees of freedom are large. Systematic patterns or trends in the residuals that may be.indicative of departures from model assumptions, and large residual values for individual cells, often are not reflected in the summary measure. Also, a good fit for a model based on a cross-classification that ignores relevant covariables does not imply that such variables are unimportant or should be considered." (pp. 137-138) Such an examination of goodness of fit and residual errors is essential in applying the appropriate statistical model, whether logistic, loglinear, or a model implicit in a Chi-square analysis (Agresti _ _ . . , 1990). However, in none of the 19 studies on spousal exposure to environmental tobacco smoke and lung cancer (Table 1 I of the first deliverable) or I 1 studies on home and workplace exposure to environmental tobacco smoke and cardiovascular disease (Table 7 of the fifth deliverable) for which linear trend was assessed was goodness of fit tested prior to trend testing. If a test for goodness of fit failed for any of these studies, it would have been inappropriate to conclude that a linear trend was present in the log odds ratio. Second, as noted above, some of the studies cited in Table 7 of the fifth deliverable on spousal and workplace exposure to environmental tobacco smoke, reported statistically significant trends with no apparent increase in heart disease risk, including Butler's examination of male workplace exposure (RRs of 1, 1.26, and 0.76 with increasing exposure), He et al. (1994) (RRs of 1, 1.16, 6

I I I I I I I report indicating that "Only the first criterion (temporal relationship) is essential to a causal relationship; with that exception, none of the criteria should be considered as either necessary or sufficient in itself." In reality, however, Dr. Brown cannot definitively demonstrate in many of the studies that a temporal relationship exists since many of the studies he evaluates are case- control (28 out of 32 lung cancer studies. 12 out of 13 workplace studies, and 5 out of 12 , cardiovascular disease studies). Further, some lung cancer studies only measured current exposure without regard for the.long latency petiod which is known to precede the development of lung cancer. Limited Evaluation of Confounding and Misclassification Despite Dr. Brown's efforts to evaluate the relevant confounders, on page 4-16 of the third deliverable concerning confounders of studies on cardiovascular disease and exposure to environmental tobacco smoke, Dr. Brown ac`.cr_owledges that ". .. the influence of some cofactors and the magnitude of their effects have not been fully investigated." Of note, in his analyses ofconfounders, Dr. Brown rigorously evaluates the statistical significance of associations between risk factors and disease and expresses concerns about multiple comparisons within studies. This appropriate level of examination, however, was not exemplified in his evaluations of environmental tobacco smoke exposure and disease in which he relied on a more qualitative, "weight of the evidence`' approach based on the number ofstudies reporting elevated odds ratios. In addition, on page 4-6 of the third deliverable, Dr. Brown acknowledges the study by Thompson and Warburton (1993), suggesting possible spousal concordance of risk factors, i.e., that nonsmoking individuals living in smoking households consume fats more frequently, drink more alcohol, eat less root vegetables and cereals, etc. Dr. Brown does not sufficiently address the issue of misclassification and its effect on relative risk. On page 3 of the first deliverable concerning workplace exposure to environmental tobacco smoke and lung cancer risk, Dr. Brown makes the assumption that "the substantial potential for imprecise exposure estimates and resultant nondifferential misclassification would tend to bias the results of workplace PTS studies toward the null hypothesis (no effect)."+ However, Dr. Brown fails to acknowledge the possibility that in these studies, the misclassification may not be nondifferential, since cases and proxies of cases may tend to overestimate workplace exposure in an attempt to find a cause for the disease. Limited Evaluation of Study Heterogeneit l Dr. Brown payslittle attention in his review to differences in details between studies, and differences in results within studies. For example. different endpoints are addressed from study to study in studies of cardiovascular disease, including ischemic heart disease mortality, total cardiovascular disease mortality, nonfatal heart disease, myocardial infarction only, and myocardial infarction or confirmed coronary stenosis on arteriography. Perhaps due to the 8 I

5.06, and 4.11 with increasing exposure). and Lee's examination of ischemic heart disease in males (RRs of 1, 0.41, and 0.41 with increasing exposure). - Third, a recent meta-analytic approach to dose-response conducted by Tweedie and Mengersen (1995) on epidemiologic studies of lung cancer and exposure to environmental tobacco smoke revealed "little indication of a consistent dose response." In this investigation. Tweedie and Mengersen first examined the dose-response in individual papers using the Armitage statistic for equality of response to different doses and two parametric models (exponential and direct linear). They found that inclusion of the unexposed group may lead to "invalid conclusions about the relationship between an increase in dose and the corresponding response" likely to be the result _ . included unexposed _ individuaTs in all of his analyses. Tweedie and of confounding; Dr. Brown . Mengersen also considered three approaches to meta-analysis--a test for equality of response across dose levels using a combination of the Armitage test statistic, imposition of a random effects model, and imposition of a fixed effects model. They demonstrated that the dose- response is flat above the zero level of exposure, implying that the only real difference is between unexposed and exposed subjects; this finding directly contradicts Dr. Brown's statements that a dose-response relationship between exposure to environmental tobacco smoke and lung cancer exists. Tweedie and Mengersen warned that a number of issues must be considered in any assessment of dose response using epidemiological data, including , _ . standardization of dose levels, the use of appropriate models, and the role of the unexposed group in inference. Fourth, in his qualitative approach, Dr. Brown also does not consider relative risks adjusted foF other risk factors for lung cancer within studies. However, any confounding factor associated with an increase in lung cancer risk also may be associated in a dose-response fashion. One must a:..o question whether it is legitimate to test for trend in studies where the test for effect is not significant and no a priori hypothesis regarding dose-response is put forth. On page 5-48 of the first deliverable on spousal exposure to environmental tobacco smoke and lung cancer risk, Dr. . Brown comments that ". . . three of the U.S _ . studies.... are statistically significant for a test of tn.nd, providing evidence for an association between ETS exposure and lung cancer even though neither was significant in a test for effect ... this occurs because the data supporting an increase in relative risk are largely at the highest exposure level." Finally, claims of a dose response must take into account the fact that neither dose nor exposure was measured in any of these studies. Moreover, the exposure categories are based on recall and are subject to bias. Limited Evaluation of Temporality I I Dr. Brown evaluates the evidence for a causal association between environmental tobacco smoke and lung cance'r according to seven specific criteria developed by a U.S. Environmental Protection Agency workshop (U.S. EPA 19$9) which include (1) temporal relationship, (2) consistency, (3) strength of association, (4) dose-response, (5) specificity of association, (6) biologic plausibility, and (7) coherence. On page 5-72 of the first deliverable on spousal exposure to environmental tobacco smoke and lung cancer risk, Dr. Brown quotes the workshop 7 ,

among never smokers and no trend in risk with the number of years exposed. The Scottish cross- sectional survey (Tunstall-Pedoe et al. 1995) relating measures of ETS (defined by self-reports of none to a lot) to self-reported coronary disease showed a statistically elevated odds ratio of 2.4, 95% Cl=1.1-4.8 (adjusted for age, housing tenure, cholesterol, and diastolic blood pressure) for doctor-diagnosed disease among never smokers who reported "a lot" of exposure. While the odds ratio for diagnosed coronary disease at the highest level of serum cotinine was consistent with that at the highest level of ETS exposure, there are problems in interpreting results from this cross-sectional survey including the temporality of exposure and outcome, possible misclassification of former smokers as never smokers, inconsistencies in results across categories of heart disease, and incomplete control for potential confounders. Thus, neither of these studies present convincing evidence for a true ETS/heart disease association and their results do not alter my conclusions stated above. I 1 Of further interest is the paper by LeVois and Lzyard (1995) in which the authors assessed publication bias in the ETS/heart disease controversy. They compared pooled relative risk estimates from 14 published studies (relative risk=1.29, 95°/aCI=1.18-1.41) and unpublished results from the prospective American Cancer Society's Cancer Prevention Studies CPS-I and CPS-II and the National Mortality Followback Survey done by the National Center for Health Statistics (relative risk=1.00, 95% CI=0.97-1.04), The pooling of these unpublished data from several large studies not only suggest that published data overestimate the association of spousal smoking and coronary disease but also show no increased risk of disease with ETS exposure. 77

.. rw arr r.. .rr r. ,r,.. r. ;rr ` r ar .. ts ..M r. 's.r r TABLE I RELIABILITY OF THE EPIDEMIOLOGIC DATA ETS AND CARDIOVASCULAR DISEASE* REFERENCES V pp 0\ p~p 0~ ~ 00 ~ O . 00 Ch O, Q` T W O, , . . . y ~p p c~ '3 L u Cr'i v ~ 0` 'r3 u ~ a ~ rn ~ ~ .-, a ~ u nf cd y a y Rr ;y ~ - QUALITY CRITERIA ~d ~ , ~ ~ ~ O; v ~ r., ~ • ~ ~ ~ ~ .n x o ~ v -a tr, W a x x x " v i x L1 a x Seatistically significant elevated risks? O O • 0 0 1 0 10 • • O 0 • 0 0 Major confounding considered? 0 0 0 0 O O O 0 O' O O • • Important biases addressed? Selection bias • 0 Inlormation bias O O O O 0 O O O O O O O Are the data internally consistent? O O • 0 0 0 0 • • • Criteria were applied to studies of home exposure, unless data from home exposures were not separately presented. " The He(sing et al. (1988)and Sandler et al. (1989) studies reported data from the same cohort. The studies were assessed in this report independently because of inconsistencies in the authors' reporting of the data. Key: 0 = no • = yes blank space - cannot ascertain '. 8IG';r"..,cgeaSoz

I I I The differences between epidemiologic data and experimental data have led to discussions as to how the statistical significance of epidemiologic data is best assessed. It is now customaty and preferred in epidemiological and observational research to estimate the summary statistic (whether odds ratio or relative risk) and to provide a confidence limit for a possible range of values around this statistic with stated confidence. When, and if, however, significance tests are used instead, the appropriate methodology is to conduct a two-tailed test. Two-tailed significance tests are formally equivalent to confidence limits. As stated by Joseph Fleiss. "If ... the investigator intends to report the results [of the test of significance] to professional colleagues, he is ethically bound to perform a two-tailed test.... Even if ... a large accumulation of published data suggests that the difference being studied should be in one direction and not the other, the investigator should nevertheless guard against the unexpected by performing a two-tailed test. Especialk• in such cases, the scientific importance of a difference in the unexpected direction may be greater than yet another confirmation of the difference being in the expected direction." (Fleiss 1981, p. 28). If an investigator believes that a one-tailed test of significance is appropriate given prior knowledge of outcome or expectations of results, the use of the test must be specified before the data are analyzed. As Selvin states, "The decision to use a one- or two-sided test must be made in advance of the data analysis. Basing the decision on information from the collected data incurs test-direction bias" (Selvin 1991, p. 44). Dr. Brown states that, "The justification for [the use of the one-tailed testj is based on the a priori hypothesis (from the plausibility of a lung cancer effect documented in Chapters 3 and 4) that a positive association exists between exposure to ETS and lung cancer." This approach is not consistent with the recommended use of a one-tailed test since Dr. Brown sets out to test the statistical significance of a null hypothesis of no effect which he has already rejected. He has clearly reached a conclusion about the significance of the data before deciding on a test of significance. Dr. Brown's decision to use a one-tailed test allowed him to estimate a 90% confidence interval rather than the conventional 95% confidence interval. This ultimately allowed him to more easily obtain an apparently significant outcome. As recognized by Bjorn Ander~en: "The advantage of a one-tailed test is that a significant outcome is easier to obtain. ... If one-tailed tests are to be used.at all, the essential requirement is that the decision is made independent of the data. Choosing a one-tailed test in order to obtain a significant result, once the direction of the 3ifference is evident from observations, is a kind of 'data dredging' approaching scientific misconduct..."(Andersen 1991, p. 235). Dr. Brown's desire to apply a 90% confidence interval is all the more surprising given the knowledge that a meta-analysis will re-inforce any systematic biases in the individual studies. As observed by LeVois and Layard (1994), the spousal smoking design is subject to positive bias and confounding, and therefore, "Given the large number of studies, all using the [same] flawed spousal smoking design, a[meta-analysisJ ... will with high probability detect the influence of 11 I