Tobacco Documents Online

226 Per iod Age LETTERS TO ~ THE EDITOR _\!f JI' \ .It~ 5l~ 2y! ~' 21, 21, \ 21, 2p N Coh FIGrRE 1; Rates for the non-linear age model. h#l- culated'in the same way as inTigure 3 ofOsmond artd Gardner (21. models onlv "work" as a result of aggregation and making assumptions of constancy of effect within an intenal!, At present„ we see two avenues for investigators who wish to trvto estimate the separate linear effec ofage. period, and cohort: 1)~use a two•wactable d impose a linear constraint, ignoring the overla ing of.eohorts: and'21 use the individualI records ap roaeh. whichidoes not have the problem of overla ,ing co• horts. This approach will reqwire a cor tion for potential bias brought about by the a mmetry in forcing the continuous data into a t~ •way table. Brown and Conelly (personal comm ication, 1988) have informed us of some very int esting work they are doing in this area. Finally, in our published ex , mple on the use of individuallrecords in, the anal 'is of lung cancer and laryngeal cancer incidence i cotland (31, the cohort effect is approximately qu ratic and the time effect small but non-linear. Su effects cannot be induced by assuming a monoto 'c increasing age effect alone. REFERENCES. 1. Tango T. Re: "Statistical modelling ofllung cancer andleryngeal cancer incidence in Scotland, 1960- 1979." Am J Epidemiol 1988;128:67 -8. 2. Osmond C. Gardner MJ. Age, per ^ and cohort models: non-overlapping eohorta on'c resolve the identification problem. Am J E' tdemiol 1989:129: 31-5. 3. Boyle P, Rohertson C. Sg4istical modelling of lung cancer and laryngelA cancer incidence in Scotland, 1960-1979. A)fi J Epidemiol' 1987;125: 731-44. 4. Osmond C; Gardnej/MJ. Age. period and cohort models applied toy4ncer mortality rates. Stat Med 1982:1:245-59. 5. Clayton D, Sc fflers E. Models for temporal var- ihtion in c cer rates: age-periodi ege•cohort models. S Med 1987;6:449-67. 6. Fienber E. Mason WM. Identification and es- timati of age-period-cohort ine the analysis of discr e and archival data. In: Schuessler KF, ed. ological'methodologv. San Francisco:,Jossey- ss, 1978:, i,/becarli.A; La Vecchia C. Age, period and cohort smodels: review of knowledge and implementation ~c GLIM~ Revista di Statistica Applicata 1987; 2W9+-410! 8. Holfprd TR. The estimation of age, period and eohot~ effects for vital rates.. Biometrics 1983; 39;3 S 1 `4. ~ Petet,Boyle Unit d/.,Anafytical Epidemiology InternttYional'Agency for Research on Cancer 15a'rour~Alberd- Thomas F-69372 [,~~omCedez 08 France Chris Rbbert~qn department o~fathematics. Unitersit-v o/ Strathclvde LiLingstone Tou•e 26 ~R~ichmond'Stre Glasgou Gl 1 XH United Kingdom AtM, 1 -A- I Ll ) Jo-_.. ~4I'`) VRE: "EFFECTS OF PASSIVE SMOKING IN THE MULTIPLE RISK FACTOR ~ Zi 6 -7 INTERVENTION TRIAL" Some of the health effects of'passive smoking may be smallj and are best investigated in large cohort studies of persons exposed over a long period; It is unfortunate that the analysis by Svendsen et al! (1):of the unique data gathered in the course ofthe Multiple Risk Factor Intervention Triall (MRFIT) study is flawed, and may introduce confusion about the role of passive smoking as a risk factor in cardiovascular disease. and does not allow the investigators to fully explore the potential, of passive smoking as a risk factor in other conditions. The Svendsen paper repeatedly tests the statistical significance of the difference between the same pro- portionlsl. For example, table 7, shows that of the 16a00 never smokers„13 men died from coronary, heart disease and 30 from any cause, and that there were 69 fatal or nonfatal coronary heart disease avents. Each group is examined for significant difference in propor- tions according to the wife's smoking status as if it were independent of the two other groups; in fact, the coronary hearu disease death group is a subset of the two other groups, and its contribution to the calcula- tiomof relative risk is,thus taken into account three times in this table. The correct analvsis would have compared 'death from other,causes- and~ "'nonfatal'. coronary hearu disease events" with "death fivm ~cor- onary heart disease". The misuse of statistics is compounded in table 9„ when the 2.222 ex-smokers are added to the 1,400 never smokers /this is my, assumption: no n's are

LE7TERS TO: THE EDITOR' 227' I given). ln this, analysis„the 13 coronary heart disease deaths in the never smokers are again included and the proportions to which they contribute are tested for statistical significance three more times. The ap, propriate analysis would have examined only the 2.222 ex-smokers in the same terms, as suggested for table 7. The reader who is interested in outcomes other than coronary hean disease death is forced: to use guesswork to subtract this effect from the other data in the tables. For example, even though we are not told the numbers of inen in table 9, the much lower p value for "death from any cause" than in table 7 suggests that this difference is due to the contribution of the ersmokers. Had these been analyzed sepa- rately, the difference in risk of "death from any cause" between the exposed and' nonexposed ex-smokers would probably have been even more markedl This would have suggested that the men who stopped smok> ing were especially susceptible to second-hand'tobacco smoke. A presentation of the data that did not lump INTERVENTION TRIAL' /1-cl C+ ) and overlap the subsets of Interest would have made such speculatiortunnecessary: The studv by Svendsen et all is presented as an exploration without hypothesis. This "blurred" anak > sis could have been avoided if this report had set out to investigate an explicit hypothesis that specified the target group and the expected endpoint. ParadoxicallY, focussing in on a specific research question and follbw• ing the method' appropriate to address that question often allows the researchers to isolateand investigate secondary or unexpected results more accurately. REr.ERENCE 1. Svendsen KH. Ku11erLH, Martin d1.1: eu.l. Effectc ofpasst.•e smkinR in.the Atuh,pk.Risk.Fanor 1merventwn Trtal. Am J Epidemiol ]96-.;126:583-95. Peter Morgan 11&Mif1 Srreet L.onark, Ontario Canodo~XUG7J;U ,/RE: 'EFFECTS OF PASSIVE SMOKING IN THE MULTIPLE RISK FACTOR Aw ~!e'lu Sven?ken et all (l):anal>ze data from the Multiple Risk FactK Intervention Trial (MRFITI stud, • and report the relative risks of various endpoint events for men who never oked in relation to spousal smoking.. They assert that eir data provide "further evidence of a potential serio health risk for a large segment of the nonsmoking po lation" (1, p. 792). This con- clusion does not appear vo be supported by the dat.a presented.. For morbidity and mors•ali! , the relative risks are not statistically signifieant, exc t for the "all deaths" category for the group combining ever smoked" and "ex-amoker" males. Since the relatt risk for "coro- nary heart disease deaths" was not st ificantly ele- vated for that group, the increased rela 've risk for "all deaths" requires some explanation befo the sta- tistics can be assumed to indicate a meanin ul in- crease in health risk related to spousal smoking. While the statistics alone raise serious doubtabo should not be disregarded, nor can statistical adjust- ments be mad'e to eliminate their possible roles. Thus, while the MRFIT study was well designed to assess the effect of various interventions according to se- lected risk factors, it does not appear to have been designed to assess the environmental tobacco smoke exposure as a coronarv heart disease risk factor. Svendsem en al. observe that men whose wives smoked' had 'significanti? lower levels of pulmonarc function at baseline" (1, p. 78fi). The authors fail„ however, to note and to interpret the data in table 6, which shows FE\•, levels for men whose wt\ es smoked 20+ cigarettes/,dae were markedl. hiFher than those of men whose wives smoked 1-19cigarettes(daY, both at baseline and4veraged over all visits. With such a notable reversaP of the dose-response relbtion, which must be demonstrated if causal inferences are to be supported• there seemF to be little basis,for suggesunp the possibility of ant• relation betM•een pulmonan function and spousal smoking from this studl. the conclusion of increased heal'th,riskfor nonsmokers exposed to environmental tobacco smoke based' on spousal smoking, questions also need to be raised about the quality of the evidence on which the assess- ments are based, notably the nonhomogeneity between the groups based'on spousal'smoking classification. The lack of homogeneity was implicit when adjust- ments were made for differences in some coronary heart disease riskiactors, e.g-, age, weight. blood pres- sure, and alcohol consumption, but there is no indi• cation that the adjustment includ'ed'consideration of the additive effect of multiple risk factors, as has been, demonstrated imnumerous other studies, notably, the Framingham Heart Study: There is no indication that other coronary heart disease risk factors, e.g., family history and exercise, were considered or adjusted for, Differences in forced expiratory volume in one second (FE\',)',among the groups were also cited. The numer- ous confuunding coronary heart disease risk facwrs The weakness of the evidence thus raisec imponant q stionsabout the conclusion that "pa~site smoking is a ciatrd with an increase in morbidit\ and mor tality ong nonsmokers- (1, p. 791). There iF cer- tainiv , n convincing demonstration that spousal smoking co titutes a "potential serious health risk- for any segme of the nonsmoking populanon RErY.RENtE 1. Ga•end•rn KH. Kultrr t,.H, \lrmn \t.l, et al Efiens nf pasnv smuk'tnc in the T~htnlh H~<1 Faci r amenrntmn Triall Am .l Apidem,nl I9n. L6 7ti+'-Ni. an \V katzenstein, lin cn..tPin Aa.uc~ares 51 R ku uod Lritr Larz•h ni. NY ]053F