0895-4356/92$5.00 + 0.00 Copyright 0 1992Pergamon Press Ltd
J Clin EpidemiolVol. 45, No. 8, pp. 809-813. 1992 Printedin Great Britain.All rightsreserved
Variance and Dissent
Presentation DUBIOUS
EVIDENCE OF HEART AND CANCER DUE TO PASSIVE SMOKING NATHAN
DEATHS
MANTEL*
Department of Mathematics and Statistics, The American University, Washington,
DC 20016, U.S.A. (Received in revised form 2 January 1992)
Cancer Environmental tobacco smoke Epidemiology Relative risk Lung cancer Passive smoking Glantz and Parmley [l] published a report, apparently commissioned by the U.S. Environmental Protection Agency, in which it was
suggested that passive smoking or environmental tobacco smoke caused 53,000 heart and cancer deaths annually in the U.S. That estimated death toll is not independently developed by Glantz and Parmley but is essentially borrowed from Wells [2], with modifications by Kawachi et al. [3]. In their own area of expertise, Glantz and Parmley claim certain physiological effects, particularly on platelets, of exposure to tobacco smoke but do not say whether those effects are unique to such exposure or that they necessarily lead to increased mortality. In the event, that work provides them with an introduction to writing about the death toll from passive smoking. That there is such a toll is taken as unquestionably a given, so attention need be paid to only the magnitude of the toll. But away from their area of expertise, Glantz and Parmley seem to be naive. Thus they take as worthy of note that the confidence intervals on relative risk in their Table 1 are skewed towards higher risks-this is essentially a necessity, since a relative risk can range upwards to *All
correspondence should be addressed to: Nathan Mantel, 11508 Regency Drive, Potomac, MD 20854, U.S.A.
Heart disease
Ischemia
infinity, but downwards only to zero. The countervailing upper limit on relative risk to a lower limit of 0.1 is 10.0. Peter Lee is credited by Glantz and Parmley with checking the statistical powers of the studies on heart disease reported in Table 1. But Lee could not have approved of the statistical powers as reported in that table. For the work by Helsing et al. [4] on females, the table shows a 2% power for detecting a relative risk of 1.2 with 95% confidence-I would have to judge that power to be more like 98%. And the 3% power shown for He [5] should perhaps be 97%. It is interesting that in Table 1 the 3 highest of 12 independent relative risks shown (respectively, 2.1, 3.6, 2.7) are associated with the 3 smallest numbers of deaths or cases (13, 2 1, 19) and with the 3 highest upper confidence limits on that risk (6.5, 13.8, 13.6). But the results of just two investigations dominate the results in Table 1, Helsing et al. [4], with 370 male cases or deaths, 988 female cases or deaths, and Hirayama [6] with 494 female cases or deaths. Perhaps the work in situations where the non-smoking spouse is the husband should be discounted. Elsewhere [7], in commenting on the work of Svendsen et al. [8], I made the point that the combination of a smoking wife with a non-smoking husband would be atypical in ways which could influence outcomes. And in 809
810
NATHAN MANTEL
such cases, a man who had never smoked might be one who had a health condition which precluded smoking. I will not dwell on this. A concern which I have expressed [9] relative to passive smoking and lung cancer, but which should also apply to passive smoking and heart deaths, is that of deceivers, the misclassification bias in which smoking women report themselves to be non-smokers or never-smokers. That bias, which would run through all the studies conducted, I noted [9] as being particularly appropriate to the work on lung cancer reported by Hirayama [lo], which was defective in yet other ways. The deficiencies in that work as regards lung cancer would also apply to his work as it relates to heart deaths [6]. Among the issues ,I raised [9] was that the Hirayama study [IO] was a cohort study of relatively long duration. Any misclassification bias would be exaggerated as women who were non-smokers at the initiation of a study could become smokers by its termination, particularly since their spouses were smokers. This criticism would also apply to the work of Helsing er al. [4], the largest study by far covered by Table 1 in Glantz and Parmley. Since Glantz and Parmley have drawn so heavily on the work of Wells [2] and that of Kawachi et al. [3] in coming to their estimated toll of mortality due to passive smoking, it is well to consider just what those authors have done. Wells reports on essentially the same epidemiologic studies covered elsewhere, but accepts that passive smoking does increase the risk of death from lung cancer, other cancer, or heart disease. The question then becomes only, by how much? The misclassification bias is discounted, so that only a minimal reduction in the apparent estimate of relative risk is made for that source of bias. But then, an important upward adjustment of relative risk is made on the basis that individuals, including even the unexposed controls, are nevertheless exposed to environmental tobacco smoke. Effects of passive smoking and of environmental tobacco smoke are taken as multiplicative, and the toll is calculated so as to include deaths from environmental tobacco smoke apart from more specific passive smoking. In any event, Wells (Table 5) shows a relative risk of lung cancer of 1.48 for females, and 2.4 for males. For heart disease the corresponding figures are 1.32 and 1.29. And in Table 7, while the toll for lung cancer, other cancer and heart
disease is calculated as in excess of 53,000, a best current compromise estimate is shown as 46,000 annual deaths. Curiously, in Wells’ Table Bl covering all causes of death in women from passive smoking, three of four studies showed either non-significant increases or even, in one study, a decrease. But that last study was impeached by Wells. Overall, the results of Table Bl were dominated by data obtained by private communication from Hirayama; 9107 out of a total of 9537 cases. Still, the estimated toll by Wells hinges on the results for passive smoking when it is only the exposure to spousal smoking which is relevant. For it is improper to make an adjustment for environmental tobacco smoke if the passive smoking effect is not clearly established or is due only to some bias. Kawachi et al. [3] take a course parallel to that of Wells, but differentiate between the toll due to passive smoking at home and that due to passive smoking in the workplace, rather than as between passive smoking, presumably at home, and other environmental tobacco smoke exposures. For exposure at home, the relative risk of lung cancer is taken as 1.3 for men, and also for women. And for deaths from ischemic heart disease, the corresponding figures are 1.3 and 1.2. Relative to exposures to passive smoking at work, the data are scanty, and only the data of Svendsen et al. [8] are cited. For heart disease deaths, while the point estimate of relative risk is high at 2.6, the data are so sparse as to make the lower limit on that relative risk below unity, actually 0.5. Kawachi et al. then had recourse to a relationship derived by Repace and Lowrey [ll, 121. Under that relationship the daily inhalation of particulate tobacco smoke was about four times as high in the workplace as at home, 1.82 vs 0.45 mg, and, combined, five times as high, at 2.27 mg daily. Accordingly, Kawachi et al. multiplied the excess risk over unity by four to get an estimate of relative risk from passive smoking in the workplace. For lung cancer, those relative risks turned out to be 2.2 both for men and for women, while for ischemic heart disease they were 2.3 and 1.9, respectively. Those relative risks of heart disease deaths from exposure to passive smoking in the workplace seem to be extravagantly high and they would be still higher if exposures to spousal smoking were added. Consider that the 1983
Presentation: Dubious Evidence of Death Due to Passive Smoking
Surgeon General’s Report [13] showed overall a 70% greater risk of death from coronary heart disease from active smoking (though that could be higher for heavy smokers, two or more packs a day). It is not reasonable that risks reported for passive smoking should exceed those for active smoking. Even Wells’ [2] estimates of the relative risk of heart deaths from passive smoking were nowhere near so high. For more on this point, Wells [14] in a letter in the Lancet cites Hammond [15] as showing active smoking to give a relative risk of heart disease of 1.5 in women, 1.7 in men, both below the relative risks computed by Kawachi et al. for passive smoking. The interest Wells had in citing these relative risks for active smoking was to show that any misclassification bias could be of only a very limited extent. Where Kawachi et al. may have gone awry was in relying on the results of Repace and Lowrey [ 11, 121or possibly in the way in which they used those results. Repace and Lowrey [ 121 did make a relatively early estimate of the toll in the U.S. of lung cancer due to passive smoking. Their estimate was based on the difference between lung cancer rates in Seventh Day Adventists, presumably then non-smokers, and lung cancer rates in non-smoking non-Seventh Day Adventists, who presumably would be exposed to passive smoking. The tacit assumption then in the estimate by Repace and Lowrey was that, relative to lung cancer, the Seventh Day Adventists and non-Seventh Day Adventists differed only in the use of cigarettes. But, of course, they differed in many other ways. As in the case with the estimated toll by Wells, the estimated toll by Kawachi et al. hinges on the demonstration of an effect of spousal passive smoking, for without that demonstrated effect there would be no basis for estimating either an environmental tobacco smoke effect or a workplace passive smoking effect. Repace and Lowrey did not demonstrate any kind of effect, they just made a calculation. But making a calculation of a mortality toll due to passive smoking does not establish that there is any toll at all. Glantz and Parmley suggest that in the various studies reported on, passive smoking effects remained even after adjustment for confounding variables, including in some cases confounders which were crude indicators of socioeconomic status, such as housing or education. However, socioeconomic status would warrant much more attention.
811
In a letter to the International Journal of Epidemiology [16], I cited results from Rona et al. [ 171 on the issue of socioeconomic status. These investigators reported, aside from an employed-unemployed differential, that smoking rates were much higher in parents in the lowest social classes. In the lowest of six social classes the paternal smoking rate was almost three times greater than in the highest social class, 62.7 vs 23.5%. For mothers, there was just about a 4-fold differential, 59.4% vs 14.8%. Perhaps that smoking differential in parents could explain the higher rate of respiratory disease in children of smoking parents. With low socioeconomic status there would be lower income, poorer housing, poorer diets, and reduced medical care, all contributing to increased respiratory illness in the children. Similarly, the wives of smoking husbands would be affected by the concomitants of socioeconomic levels. And all of these could contribute to an extent in the increased frequency of heart and cancer deaths in the non-smoking wives of smokers from the lower social class. On the point of social class, Kaplan and Salonen [ 181 have reported a study in which individuals who were in the lowest third of socioeconomic conditions as children had a statistically significant, 44%, increase in ischemia on exercise later in life as compared with individuals who were in the highest third. The analysis had been adjusted for age, but when additional adjustment was made for other factors, including particularly the later use of cigarettes by those children, the estimate of added risk of ischemia on exercise due to low childhood socioeconomic status was little changed. If even active smoking cannot explain away the effect of low socioeconomic status, it can reasonably be expected, and as I must imagine to be true, that low socioeconomic status will substantially account for any apparent effects of passive smoking. Striking results are given in a report by Svendsen er al. [8], the smallest of the studies covered in Glantz and Parmley. Apparently, where it is the never-smoking husband who is exposed to passive smoking due to smoking by the wife, the relative risk of coronary heart disease death is increased by a factor of 2.11 unadjusted, or 2.23 adjusted for certain confounders. Even the risk of death from any cause is closely doubled. But even Kawachi et al. had reported a relative risk of only 1.3 for passive smoking exposures at home, the relative risk of
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NATHANMANTEL
2.3 pertaining to passive smoking exposures in the workplace. The relative risk by Svendsen et al. [19] which presumably pertains to only a small fraction of passive smoking, even exceeds the relative risk alluded to above of 1.7 for active smoking. Perhaps the answer lies in the suggestion I gave above that the non-smoking husbands of smoking wives were already in poor health. If Svendsen et al. did not view their relative risk estimates as unusually high, it may be because they were influenced by the results of Garland et al. [19] whom Glantz and Parmley report as showing a relative risk of 2.7 for passive smoking in women (not statistically significant at the 0.05 level). But Glantz and Parmley do not show that the 2.7 relative risk was a downward correction from an originally published relative risk by Garland et al. of almost 15. While Svendsen et al. cite Garland et al., they do not show their actual relative risk figures. Perhaps the timing was such that the manuscript by Svendsen et al. was submitted and accepted before the corrigendum appeared. Actually, relative to Garland et al., I wrote a letter to the American Journal of Epidemiology under the title “Bricks without straw.” It was initially accepted for publication but that acceptance was withdrawn following the submission of a corrigendum by Garland. Though it is not specifically stated in the corrigendum, the error was in mistaking the estimated relative risk as a log relative risk, then exponentiating it to come up with an estimated relative risk of about 15. Highly qualified epidemiologic investigators, like everyone else, are subject to numerical errors. This Garland et al. episode may have some bearing on an issue I have raised earlier [20], publication bias, an issue which was developed further by Vandenbroucke [21]. Given the weakness of the supporting data, would Garland et al. have even submitted their manuscript, or even have let it go through unchecked were they not so pleased with the results, which did prove to be erroneous. The publishing journal itself displayed a publication bias, favoring articles which display extreme or extravagant results. This was an example of the “right side of the issue” phenomenon which I describe elsewhere [71* Some kind of bias was operative in the recent past when the media (newspapers and television) carried stories to the effect that where both parents smoked, the child in later life was at
significantly increased risk of lung cancer. But the underlying study, reported in the New England Journal of Medicine (Janerich et al. [22]), provided no information on whether either or both parents smoked. While as reported in the media, the impression was that the effect of passive smoking was being confirmed, the actual published report was, in a sense, exculpatory. No effect was found either for spousal passive smoking or for passive smoking in the workplace. Further, passive smoking in social settings was found to be significantly protective against lung cancer. As for the two-smoking parent effect, this was a journalistic extrapolation. The increased lung cancer effect applied if the individual was exposed to at least 25 person-years of passive smoking prior to attaining age 21, and that was interpreted by journalists to mean that both parents must have been smokers, for how else have 25 person-years of exposure by age 21. The authors of the underlying study [22] had in mind to show that it was exposure to passive smoking in childhood that mattered, not later exposure whether to spousal smoking or passive smoking in the workplace. Yet, even so, just as Kaplan and Salonen [18] found an increased risk of ischemia in later life for individuals raised as children under low socioeconomic conditions, the same would be true now relative to lung cancer. Heavier or more frequent smoking by parents would betoken a poorer socioeconomic status for the family. Wells [23] and also Kawachi and Pearce [24] have suggested that criticism by Peter Lee on the passive smoking issue could be impeachable, characterizing Lee as a tobacco consultant or as working on behalf of the tobacco industry. Since so much of the anti-passive smoking or anti-environmental tobacco smoke work is faulty and impeachable, the tobacco industry must turn to highly qualified statisticians like Peter Lee to examine that work carefully. There is a wide difference in attitude between statisticians and epidemiologists. The statistician is the more concerned with the convincingness of a study, considering both chance variation and possible biases. But, perhaps with an eye to chance variation, the epidemiologist primarily judges whether he/she would have been ready to submit the instant report for publication-he/she does not judge so critically, as he/she would not want his/her own work to be judged.
Presentation: Dubious Evidence of Death Due to Passive Smoking
What surprises me in all this affair is the intensity with which the US. Environmental Protection Agency has been pursuing the issue-maybe it is only a few officials in the Agency who are responsible. Where a panel comes out with a positive finding for the ill effects of passive smoking, it is not so much the data or the studies which are convincing, but rather a logical extrapolation of the effects of active smoking. I am not suggesting that anyone change his/her mind about whether passive smoking causes cancer or heart deaths. They are free to retain their opinions or beliefs. But they should understand that the case has not been properly proven. What has been claimed is largely, or mostly, or even completely fiction. Let me say further that I have become suspicious of reports carried out by or for government agencies like the U.S. Environmental Protection Agency. In [7], I alluded to a study linking spontaneous abortion to forest spraying with Agent Orange. Without proper justification, the authors simply asserted that there was a significant link-those authors knew what their master, the Government Agency, wanted.
7.
8.
9.
10.
11.
12.
13.
14. 15.
16. 17.
18. REFERENCES Glantz SA, Parmley WW. Passive smoking and heart disease-epidemiology, physiology and biochemistry. Circulation 1991; 83: I-12. 2. Wells AJ. An estimate of adult mortality in the United States from passive smoking. Environ Int 1988; 14: 249-265. 3. Kawachi I, Pearce NE, Jackson RT. Deaths from lung cancer and ischaemic heart disease due to passive smoking in New Zealand. NZ Med J 1989; 102: 3377340. 4. Helsing KJ, Sandier DP, Comstock GW, Chee E. Heart disease mortality in nonsmokers living with smokers. Am J Epidemiol 1988; 127: 915-922. 5. He Y. Women’s passive smoking and coronary heart disease. Chun Hua-Yu-Fang-I-Hsueh-Tsa-Chin 1989; 23: 19-22. (Translation.) 6. Hirayama T. Lung cancer in Japan: Effects of nutrition and passive smoking. In: Mizell M, Correa P, Eds. 1.
19.
20.
21. 22.
23.
24.
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Lung Cancer: Causes and Prevention. New York, Verlag Chemie International; 1984: 175-195. Mantel N. The passive smoking myth. In: Bieva GJ, Courtois Y, Govaerts M, Eds. Present and Future of Indoor Air Qua@. Amsterdam: Excerpta Medica; 1989: 155-159. Svendsen KH, Kuller LH, Martin MJ, Ockene JK. Effects of passive smoking in the multiple risk factor intervention trial. Am J Epidemiol 1987; 126: 783-795. Mantel N. Epidemiologic investigations: Care in conduct, care in analysis and care in reporting. J Cancer Res CIIn One01 1983; 105: 113-116. Hirayama T. Non-smoking wives of heavy smokers have a higher risk of lung cancer: A study from Japan. Br Med J 1981; 282: 183-185. Repace JL, Lowrey AH. A quantitative estimate of nonsmokers lung cancer risk from passive smoking. Environ Int 1985; 11: 3-22. Repace JL, Lowrey AH. Predicting the lung cancer risk of domestic passive smoking. Am Rev Resp Dis 1987; 136: 1308. US Public Health Service. The Health Consequencesof Smoking: Cardiovascular Disease: A Report of the Surgeon General. DHHS (PHS) 84-50204; 1983. Wells AJ. Misclassification as a factor in passive smoking risk. (Letter.) Lancet 1986; 2: 638. Hammond C. Smoking in relation to the death rates of one million men and women. In: Haenszel W, Ed. Epidemiological Approaches to the Study of Cancer and Other Chronic Diseases. Nat1 Cancer Inst Monograph 1966; No. 19: 127-204. Mantel N. Does passive smoking stunt the growth of children? (Letter.) Int J Epidemiol 1986; 15: 427428. Rona RJ, Chinn S, Florey CDV. Exposure to cigarette smoking and children’s growth. Int J Epidemiol 1985; 14: 402409. Kaplan GA, Salonen JT. Socioeconomic conditions in childhood and ischaemic heart disease during middle age. Br Med J 1990; 301: 1121-1124. Garland C, Barrett-Connor L, Suarez L, Criqui MH, Wingard DL. Effects of passive smoking on ischemic heart disease mortality of nonsmokers-a prospective study. Am J Epidemiol 1985; 121: 645650. Mantel N. What is the epidemiologic evidence for a passive smoking-lung cancer association? In: Kasuga H, Ed. Indoor Air Quality. Berlin: Springer-Verlag; 1990: 341-347. Vandenbroucke JP. Passive smoking and lung cancer: a publication bias? Br Med J 1988; 296: 391. Janerich DT, Thompson WD, Varela LR er al. Lung cancer and exposure to tobacco smoke in the household. N Engl J Med 1990; 323: 632426. Wells AJ. An estimate of adult mortality in the United States from passive smoking: A response to criticism. (Letter.) Environ Int 1990; 16: 187-193. Kawachi I, Pearce N. Passive smoking in New Zealand. (Letter.) NZ Med J 1989; 102: 479.
J Clin EpidemiolVol. 45, No. 8, pp. 809-813. 1992 Printedin Great Britain.All rightsreserved
Variance and Dissent
Presentation DUBIOUS
EVIDENCE OF HEART AND CANCER DUE TO PASSIVE SMOKING NATHAN
DEATHS
MANTEL*
Department of Mathematics and Statistics, The American University, Washington,
DC 20016, U.S.A. (Received in revised form 2 January 1992)
Cancer Environmental tobacco smoke Epidemiology Relative risk Lung cancer Passive smoking Glantz and Parmley [l] published a report, apparently commissioned by the U.S. Environmental Protection Agency, in which it was
suggested that passive smoking or environmental tobacco smoke caused 53,000 heart and cancer deaths annually in the U.S. That estimated death toll is not independently developed by Glantz and Parmley but is essentially borrowed from Wells [2], with modifications by Kawachi et al. [3]. In their own area of expertise, Glantz and Parmley claim certain physiological effects, particularly on platelets, of exposure to tobacco smoke but do not say whether those effects are unique to such exposure or that they necessarily lead to increased mortality. In the event, that work provides them with an introduction to writing about the death toll from passive smoking. That there is such a toll is taken as unquestionably a given, so attention need be paid to only the magnitude of the toll. But away from their area of expertise, Glantz and Parmley seem to be naive. Thus they take as worthy of note that the confidence intervals on relative risk in their Table 1 are skewed towards higher risks-this is essentially a necessity, since a relative risk can range upwards to *All
correspondence should be addressed to: Nathan Mantel, 11508 Regency Drive, Potomac, MD 20854, U.S.A.
Heart disease
Ischemia
infinity, but downwards only to zero. The countervailing upper limit on relative risk to a lower limit of 0.1 is 10.0. Peter Lee is credited by Glantz and Parmley with checking the statistical powers of the studies on heart disease reported in Table 1. But Lee could not have approved of the statistical powers as reported in that table. For the work by Helsing et al. [4] on females, the table shows a 2% power for detecting a relative risk of 1.2 with 95% confidence-I would have to judge that power to be more like 98%. And the 3% power shown for He [5] should perhaps be 97%. It is interesting that in Table 1 the 3 highest of 12 independent relative risks shown (respectively, 2.1, 3.6, 2.7) are associated with the 3 smallest numbers of deaths or cases (13, 2 1, 19) and with the 3 highest upper confidence limits on that risk (6.5, 13.8, 13.6). But the results of just two investigations dominate the results in Table 1, Helsing et al. [4], with 370 male cases or deaths, 988 female cases or deaths, and Hirayama [6] with 494 female cases or deaths. Perhaps the work in situations where the non-smoking spouse is the husband should be discounted. Elsewhere [7], in commenting on the work of Svendsen et al. [8], I made the point that the combination of a smoking wife with a non-smoking husband would be atypical in ways which could influence outcomes. And in 809
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NATHAN MANTEL
such cases, a man who had never smoked might be one who had a health condition which precluded smoking. I will not dwell on this. A concern which I have expressed [9] relative to passive smoking and lung cancer, but which should also apply to passive smoking and heart deaths, is that of deceivers, the misclassification bias in which smoking women report themselves to be non-smokers or never-smokers. That bias, which would run through all the studies conducted, I noted [9] as being particularly appropriate to the work on lung cancer reported by Hirayama [lo], which was defective in yet other ways. The deficiencies in that work as regards lung cancer would also apply to his work as it relates to heart deaths [6]. Among the issues ,I raised [9] was that the Hirayama study [IO] was a cohort study of relatively long duration. Any misclassification bias would be exaggerated as women who were non-smokers at the initiation of a study could become smokers by its termination, particularly since their spouses were smokers. This criticism would also apply to the work of Helsing er al. [4], the largest study by far covered by Table 1 in Glantz and Parmley. Since Glantz and Parmley have drawn so heavily on the work of Wells [2] and that of Kawachi et al. [3] in coming to their estimated toll of mortality due to passive smoking, it is well to consider just what those authors have done. Wells reports on essentially the same epidemiologic studies covered elsewhere, but accepts that passive smoking does increase the risk of death from lung cancer, other cancer, or heart disease. The question then becomes only, by how much? The misclassification bias is discounted, so that only a minimal reduction in the apparent estimate of relative risk is made for that source of bias. But then, an important upward adjustment of relative risk is made on the basis that individuals, including even the unexposed controls, are nevertheless exposed to environmental tobacco smoke. Effects of passive smoking and of environmental tobacco smoke are taken as multiplicative, and the toll is calculated so as to include deaths from environmental tobacco smoke apart from more specific passive smoking. In any event, Wells (Table 5) shows a relative risk of lung cancer of 1.48 for females, and 2.4 for males. For heart disease the corresponding figures are 1.32 and 1.29. And in Table 7, while the toll for lung cancer, other cancer and heart
disease is calculated as in excess of 53,000, a best current compromise estimate is shown as 46,000 annual deaths. Curiously, in Wells’ Table Bl covering all causes of death in women from passive smoking, three of four studies showed either non-significant increases or even, in one study, a decrease. But that last study was impeached by Wells. Overall, the results of Table Bl were dominated by data obtained by private communication from Hirayama; 9107 out of a total of 9537 cases. Still, the estimated toll by Wells hinges on the results for passive smoking when it is only the exposure to spousal smoking which is relevant. For it is improper to make an adjustment for environmental tobacco smoke if the passive smoking effect is not clearly established or is due only to some bias. Kawachi et al. [3] take a course parallel to that of Wells, but differentiate between the toll due to passive smoking at home and that due to passive smoking in the workplace, rather than as between passive smoking, presumably at home, and other environmental tobacco smoke exposures. For exposure at home, the relative risk of lung cancer is taken as 1.3 for men, and also for women. And for deaths from ischemic heart disease, the corresponding figures are 1.3 and 1.2. Relative to exposures to passive smoking at work, the data are scanty, and only the data of Svendsen et al. [8] are cited. For heart disease deaths, while the point estimate of relative risk is high at 2.6, the data are so sparse as to make the lower limit on that relative risk below unity, actually 0.5. Kawachi et al. then had recourse to a relationship derived by Repace and Lowrey [ll, 121. Under that relationship the daily inhalation of particulate tobacco smoke was about four times as high in the workplace as at home, 1.82 vs 0.45 mg, and, combined, five times as high, at 2.27 mg daily. Accordingly, Kawachi et al. multiplied the excess risk over unity by four to get an estimate of relative risk from passive smoking in the workplace. For lung cancer, those relative risks turned out to be 2.2 both for men and for women, while for ischemic heart disease they were 2.3 and 1.9, respectively. Those relative risks of heart disease deaths from exposure to passive smoking in the workplace seem to be extravagantly high and they would be still higher if exposures to spousal smoking were added. Consider that the 1983
Presentation: Dubious Evidence of Death Due to Passive Smoking
Surgeon General’s Report [13] showed overall a 70% greater risk of death from coronary heart disease from active smoking (though that could be higher for heavy smokers, two or more packs a day). It is not reasonable that risks reported for passive smoking should exceed those for active smoking. Even Wells’ [2] estimates of the relative risk of heart deaths from passive smoking were nowhere near so high. For more on this point, Wells [14] in a letter in the Lancet cites Hammond [15] as showing active smoking to give a relative risk of heart disease of 1.5 in women, 1.7 in men, both below the relative risks computed by Kawachi et al. for passive smoking. The interest Wells had in citing these relative risks for active smoking was to show that any misclassification bias could be of only a very limited extent. Where Kawachi et al. may have gone awry was in relying on the results of Repace and Lowrey [ 11, 121or possibly in the way in which they used those results. Repace and Lowrey [ 121 did make a relatively early estimate of the toll in the U.S. of lung cancer due to passive smoking. Their estimate was based on the difference between lung cancer rates in Seventh Day Adventists, presumably then non-smokers, and lung cancer rates in non-smoking non-Seventh Day Adventists, who presumably would be exposed to passive smoking. The tacit assumption then in the estimate by Repace and Lowrey was that, relative to lung cancer, the Seventh Day Adventists and non-Seventh Day Adventists differed only in the use of cigarettes. But, of course, they differed in many other ways. As in the case with the estimated toll by Wells, the estimated toll by Kawachi et al. hinges on the demonstration of an effect of spousal passive smoking, for without that demonstrated effect there would be no basis for estimating either an environmental tobacco smoke effect or a workplace passive smoking effect. Repace and Lowrey did not demonstrate any kind of effect, they just made a calculation. But making a calculation of a mortality toll due to passive smoking does not establish that there is any toll at all. Glantz and Parmley suggest that in the various studies reported on, passive smoking effects remained even after adjustment for confounding variables, including in some cases confounders which were crude indicators of socioeconomic status, such as housing or education. However, socioeconomic status would warrant much more attention.
811
In a letter to the International Journal of Epidemiology [16], I cited results from Rona et al. [ 171 on the issue of socioeconomic status. These investigators reported, aside from an employed-unemployed differential, that smoking rates were much higher in parents in the lowest social classes. In the lowest of six social classes the paternal smoking rate was almost three times greater than in the highest social class, 62.7 vs 23.5%. For mothers, there was just about a 4-fold differential, 59.4% vs 14.8%. Perhaps that smoking differential in parents could explain the higher rate of respiratory disease in children of smoking parents. With low socioeconomic status there would be lower income, poorer housing, poorer diets, and reduced medical care, all contributing to increased respiratory illness in the children. Similarly, the wives of smoking husbands would be affected by the concomitants of socioeconomic levels. And all of these could contribute to an extent in the increased frequency of heart and cancer deaths in the non-smoking wives of smokers from the lower social class. On the point of social class, Kaplan and Salonen [ 181 have reported a study in which individuals who were in the lowest third of socioeconomic conditions as children had a statistically significant, 44%, increase in ischemia on exercise later in life as compared with individuals who were in the highest third. The analysis had been adjusted for age, but when additional adjustment was made for other factors, including particularly the later use of cigarettes by those children, the estimate of added risk of ischemia on exercise due to low childhood socioeconomic status was little changed. If even active smoking cannot explain away the effect of low socioeconomic status, it can reasonably be expected, and as I must imagine to be true, that low socioeconomic status will substantially account for any apparent effects of passive smoking. Striking results are given in a report by Svendsen er al. [8], the smallest of the studies covered in Glantz and Parmley. Apparently, where it is the never-smoking husband who is exposed to passive smoking due to smoking by the wife, the relative risk of coronary heart disease death is increased by a factor of 2.11 unadjusted, or 2.23 adjusted for certain confounders. Even the risk of death from any cause is closely doubled. But even Kawachi et al. had reported a relative risk of only 1.3 for passive smoking exposures at home, the relative risk of
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2.3 pertaining to passive smoking exposures in the workplace. The relative risk by Svendsen et al. [19] which presumably pertains to only a small fraction of passive smoking, even exceeds the relative risk alluded to above of 1.7 for active smoking. Perhaps the answer lies in the suggestion I gave above that the non-smoking husbands of smoking wives were already in poor health. If Svendsen et al. did not view their relative risk estimates as unusually high, it may be because they were influenced by the results of Garland et al. [19] whom Glantz and Parmley report as showing a relative risk of 2.7 for passive smoking in women (not statistically significant at the 0.05 level). But Glantz and Parmley do not show that the 2.7 relative risk was a downward correction from an originally published relative risk by Garland et al. of almost 15. While Svendsen et al. cite Garland et al., they do not show their actual relative risk figures. Perhaps the timing was such that the manuscript by Svendsen et al. was submitted and accepted before the corrigendum appeared. Actually, relative to Garland et al., I wrote a letter to the American Journal of Epidemiology under the title “Bricks without straw.” It was initially accepted for publication but that acceptance was withdrawn following the submission of a corrigendum by Garland. Though it is not specifically stated in the corrigendum, the error was in mistaking the estimated relative risk as a log relative risk, then exponentiating it to come up with an estimated relative risk of about 15. Highly qualified epidemiologic investigators, like everyone else, are subject to numerical errors. This Garland et al. episode may have some bearing on an issue I have raised earlier [20], publication bias, an issue which was developed further by Vandenbroucke [21]. Given the weakness of the supporting data, would Garland et al. have even submitted their manuscript, or even have let it go through unchecked were they not so pleased with the results, which did prove to be erroneous. The publishing journal itself displayed a publication bias, favoring articles which display extreme or extravagant results. This was an example of the “right side of the issue” phenomenon which I describe elsewhere [71* Some kind of bias was operative in the recent past when the media (newspapers and television) carried stories to the effect that where both parents smoked, the child in later life was at
significantly increased risk of lung cancer. But the underlying study, reported in the New England Journal of Medicine (Janerich et al. [22]), provided no information on whether either or both parents smoked. While as reported in the media, the impression was that the effect of passive smoking was being confirmed, the actual published report was, in a sense, exculpatory. No effect was found either for spousal passive smoking or for passive smoking in the workplace. Further, passive smoking in social settings was found to be significantly protective against lung cancer. As for the two-smoking parent effect, this was a journalistic extrapolation. The increased lung cancer effect applied if the individual was exposed to at least 25 person-years of passive smoking prior to attaining age 21, and that was interpreted by journalists to mean that both parents must have been smokers, for how else have 25 person-years of exposure by age 21. The authors of the underlying study [22] had in mind to show that it was exposure to passive smoking in childhood that mattered, not later exposure whether to spousal smoking or passive smoking in the workplace. Yet, even so, just as Kaplan and Salonen [18] found an increased risk of ischemia in later life for individuals raised as children under low socioeconomic conditions, the same would be true now relative to lung cancer. Heavier or more frequent smoking by parents would betoken a poorer socioeconomic status for the family. Wells [23] and also Kawachi and Pearce [24] have suggested that criticism by Peter Lee on the passive smoking issue could be impeachable, characterizing Lee as a tobacco consultant or as working on behalf of the tobacco industry. Since so much of the anti-passive smoking or anti-environmental tobacco smoke work is faulty and impeachable, the tobacco industry must turn to highly qualified statisticians like Peter Lee to examine that work carefully. There is a wide difference in attitude between statisticians and epidemiologists. The statistician is the more concerned with the convincingness of a study, considering both chance variation and possible biases. But, perhaps with an eye to chance variation, the epidemiologist primarily judges whether he/she would have been ready to submit the instant report for publication-he/she does not judge so critically, as he/she would not want his/her own work to be judged.
Presentation: Dubious Evidence of Death Due to Passive Smoking
What surprises me in all this affair is the intensity with which the US. Environmental Protection Agency has been pursuing the issue-maybe it is only a few officials in the Agency who are responsible. Where a panel comes out with a positive finding for the ill effects of passive smoking, it is not so much the data or the studies which are convincing, but rather a logical extrapolation of the effects of active smoking. I am not suggesting that anyone change his/her mind about whether passive smoking causes cancer or heart deaths. They are free to retain their opinions or beliefs. But they should understand that the case has not been properly proven. What has been claimed is largely, or mostly, or even completely fiction. Let me say further that I have become suspicious of reports carried out by or for government agencies like the U.S. Environmental Protection Agency. In [7], I alluded to a study linking spontaneous abortion to forest spraying with Agent Orange. Without proper justification, the authors simply asserted that there was a significant link-those authors knew what their master, the Government Agency, wanted.
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18. REFERENCES Glantz SA, Parmley WW. Passive smoking and heart disease-epidemiology, physiology and biochemistry. Circulation 1991; 83: I-12. 2. Wells AJ. An estimate of adult mortality in the United States from passive smoking. Environ Int 1988; 14: 249-265. 3. Kawachi I, Pearce NE, Jackson RT. Deaths from lung cancer and ischaemic heart disease due to passive smoking in New Zealand. NZ Med J 1989; 102: 3377340. 4. Helsing KJ, Sandier DP, Comstock GW, Chee E. Heart disease mortality in nonsmokers living with smokers. Am J Epidemiol 1988; 127: 915-922. 5. He Y. Women’s passive smoking and coronary heart disease. Chun Hua-Yu-Fang-I-Hsueh-Tsa-Chin 1989; 23: 19-22. (Translation.) 6. Hirayama T. Lung cancer in Japan: Effects of nutrition and passive smoking. In: Mizell M, Correa P, Eds. 1.
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