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This subject has long been bedevilled by unwarrantable assumption and circular argument. Why should there be only two possible hypotheses of interaction (additive and multiplicative)? Theory expects multiplicativity; epidemiology can seldom reject this hypothesis; so theory is “accepted”, and deviations from multiplicativity must be explained away. Resolution is made especially difficult because the nature of the data imposes very large error; also it has to be assumed that the exposed smoked as many cigarettes as the unexposed, and that smokers and non-smokers were exposed equally.
From almost 40 “results” in 25 reports, Lee makes two selections to confirm the well known facts that asbestos can increase lung cancer risk in non-smokers and that the additive theory (of independent action) does not explain many of the data. Then, for 16 results, Lee calculates a statistic V; for an observed multiplicative interaction, V = 1. The weighted average V = 0.90 (95% CI: 0.67 to 1.20) leads to Lee's conclusion.1 Repair of (acknowledged) imperfections (one misquoted result; two incorrect omissions) reduced V only slightly, to 0.83 (95% CI: 0.63 to 1.08); for nine cohorts and nine case–referent studies, respectively, V = 0.63 and 1.08, a “significant” difference (p = 0.049).
There are, however, other imperfections: two cohorts3,4 broke the rule of independence; in another,5 asbestos had a minuscule (protective) effect on lung cancer in both non-smokers and smokers (that is, no action, so no interaction); and in a Chinese cohort,6 risks from cigarette smoke were dramatically lower than in the West. After exclusion, the cohorts' V = 0.54 (95% CI: 0.35–0.82), and the difference between types is much wider (p = 0.017).
Problems with case–referent designs are well known; here they are compounded by impure definitions of non-smokers and by retrospective assessment of exposure. It is clear from personal experience over five decades that, unless obtained from employers' records, job histories can be quite unreliable, even in basic facts, especially when reported by proxies. The assumption that the interactions between smoking and exposure to asbestos plus other carcinogens and between smoking and asbestos alone take the same form is untested and so indefensible. Thus, Lee's grounds for his unprecedented incorporation of the Italian study in which all concerned were exposed to PAHs,7 namely, that subjects in many studies would have been exposed to “other” carcinogens, far from justifying inclusion, provide strong additional reasons for excluding all such studies, the majority of the case–referent studies in particular. It becomes obvious that inferences from the latter cannot overthrow conclusions from the cohorts.
The potential risks from dusty coal reinforce the need to exclude the Chinese cohort.6 Undoubtedly, the North American insulation workers were not exposed only to 4–12 fibres/ml of chrysotile,8 so there is a good case for discarding this result, although it forms a cornerstone of the evidence for multiplicativity. On the other hand, the study of crocidolite miners9 might be taken into account, despite faults.2 The resultant is V = 0.47 (95% CI: 0.29 to 0.75).
Lee proceeds from V = 0.83 (for 18 studies), noting that the significance of the difference between study types is not great, and “is removed” by an (admittedly dubious) adjustment of the lowest V. He “sides with other reviewers” and includes all data, concluding that “they do not clearly allow rejection of the simple multiplicative relationship”.
Despite some doubt about the “best” estimate of V from cohort studies, most reasonable people would accept that it is <1, as shown even by Lee's V = 0.63, with p = 0.018.
Therefore, the multiplicative hypothesis is not generally satisfactory. Nor, of course, is the additive hypothesis, although it does fit some data sets very well.10
Evidently, interaction takes several forms.
Having read Liddell's paper1 and the comments he expressed in his letter and at a recent meeting, it is useful to clarify where we agree and disagree. Originally I included estimates 1–16 shown in table 1, and estimated V, the ratio of the asbestos relative risk in smokers to that in non-smokers, as 0.90 (95% CI: 0.67 to 1.20). Omitting estimate 18 was an unfortunate error, and I also agree with Liddell that it is better to include estimate 17 and replace estimate 13 by estimate 19. Accounting for this reduces V to 0.83 (95% CI: 0.63 to 1.08).
Liddell also suggests excluding estimates 4, 11, 12, and 14, but for reasons I consider unconvincing. He would exclude estimate 4 as the population was exposed to PAHs. However, virtually all populations have exposure to carcinogens other than asbestos or tobacco smoke and anyway exposure to other carcinogens may simply multiply risk by about the same factor in each of the four groups being studied, little affecting the nature of the joint relation of asbestos and smoking to lung cancer. He would exclude estimate 11 because of low smoking risks, but these are typical of China2 and do not invalidate the study. He would exclude estimate 12 as no asbestos effect was seen, but doing so based on observed results can cause bias. He would exclude estimate 14 as the study population is a subset of that for estimate 15. However, the follow up period was much longer for estimate 14 (1943–74) than for estimate 15 (1967–76), so omitting it would have lost data. Anyway, omitting estimates 4, 11, 12, and 14 only has a minor effect, V reducing to 0.79 (95% CI: 0.59 to 1.05) (table 1).
At face value, the combined data appear reasonably homogeneous and compatible with the multiplicative model. However, as Liddell notes, estimates for prospective and case–control studies differ. Using my revised analysis, prospective studies give V = 0.63 (95% CI: 0.43 to 0.92) and case–control studies V = 1.08 (95% CI: 0.74 to 1.59), a statistically significant difference (p = 0.049). With Liddell's four suggested exclusions, V = 0.54 (95% CI: 0.35 to 0.82) for prospective studies and V = 1.09 (95% CI: 0.74 to 1.60) for case–control studies, with p = 0.017.
He stresses this significant difference, rejects the case–control data due to data unreliability, use of proxies, and inclusion of ex or light smokers in the reference group and argues that inferences should be drawn only from the prospective studies. I regard these arguments as dubious. The significance of the difference is not great and is removed (p = 0.089 for the revised data) if the estimate of V for the one study (estimate 15) showing a very low value is revised based on “best available evidence” rather than on death certificate diagnosis (though this revision is itself questionable). Prospective studies may be limited by failure to record changes in smoking status after follow up starts. The Quebec prospective study3 obtained data from proxies; many case–control studies did not. While data on accuracy of exposure is no doubt better in prospective studies, I side with other reviewers in considering the whole data.
The asbestos relative risk may be somewhat lower in smokers than non-smokers, but the available data do not clearly reject the simple multiplicative relation. More complex models of joint action might indeed fit the data better, but in view of the general problems with the data, it seems doubtful whether more detailed statistical analysis would shed any greater insight.
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