Tobacco Documents Online

~ ,03-NOU-1999 15:30 GALLAHER CORPORATE AFFRS "01932832532 P.O4/2G 4.L3 Data included ~om the studies selected The age adjusted rdativc risks and cordidcnce intervals used in the mcta-a~alysis ar¢only given in Figure 1 of Law, Morris and Waid and not as precise numbers in a t~ble. Also not presented are the individual sex estimates which have been combined together in Figure 1. Comparing the dat~ in Figure | with the data from the source papers, as given in Lec (I997), reveals some apparent ~nomalies: _T.unstall_-P~cdg_¢~¢! al (19955 : The confidence limits s~m too narrow compared with th0s~ estimated by Lee (1987) Who gives 1.32 (1.03-I .69) for unadjusted data and 1.37 • (I.07-1.75) for data adjusted for age and housing tenure. Could they have been calcu[at~.d falsely assuming the relative risks by level ~e independent? _M~uscat and W_~vnder f1995"~ : The relative risk given appears to be about 1.7. This seems inconsistent with the relative risks for spousal smoking, calculated from Table 1 of the sdurce paper which are 1.38 (0.70-2.75) for males and 1.33 (0.59-2.99) for females. S~ecnland et al (L995:} : The relative risk estimate, given in the discussion section of the paper, of 1.21 (I.06-1.3g), is based on a special analysis restricted to subjects concordant f0.r both self-reported current exposure to cigarettes and exposure to cigarettes based on spouse report. This involves only 1606 II-ID deaths compared with 38 I9 I'I,ID deaths in the analyses based only on spouse report. In viewofthe possible unrepresentativeness of the subsarnple of Subjects with the fuller information it would seem possibly better to have based the meta-analyse, on the spouse report data (as did Lee, ] 997). Kawachi et alC1996a.b) :Thc confidence limits again seem too narrow. They appear td have been 6alculat~ by meta-analysing results presented in Kawachi et al (I996a) for occasional ET$ exposure (1.58, 0.93-2.68) and for regular ETS cxposure (I.9I, 1,1 I- 3.28), wrongly assuming ~he e, timatcs arc independent, when they are not, and ignoring the combined estimate of 1,71 (1.03-7..84) given in Kawachi et al (I 996b). CirurA et al (19961 : The .some paper gives an estimate of 1.43 (0.9 to 2.0) which is not

~03-NOU-199~ 4.1.4 15:31 GRLLRHER CORPORATE AFFRS 01932832532 P.05/26 significant. significant. I2 Figure [ wrangly gives a lower confidence limit of" about !. 15 which is Apart from noting that there appears to have be=n a statisical error made in deriv.ing Icvd-combined rclative risks and confidcnc~ intervals from level-specific relative risk3 mad confidcnco intervals, two other general conclusions can be drawn from checking the data in Figure I of Law. Morris and Wald back to source. First, although the relative risks ~re stated to be for spousal smoking, a number ofst0dics used different indices of exposure (s~¢ Table 2 of Lee, 1997). Second, although the r, lative risks are stated to bc adjusted for age and sex, many are riot. For about half the studies it is only possible to derive either totally unadjusted i-elative risks or r~lative risks ~justcd both for age and a variable list of heart dise2se risk famors. Law, Morris and Wald givc no details of how they decided which relative risk to u~ in these circumsmncrs. EffeCt ofchoice of_study and data on the m~ta-ana!vsis relative risk estimate. Compared with Law, Morris and Wald's recta-analysis relative risk estimate of 1.30{1.22 to t.38), Lcc (1997) estimamd substantially lower risks, especially using fixed cffc~ts meta-analysis. index Relative risks (95% CI) Adjmt~ for Fixed cff~ts cov~at~s* Random effects Ever ,smoking No 1.02(0.99-I .06) 1.20(I.07-138) by th9 spouse Yes 1.07(I.03=I.I0) 1.18(I.09-I 32) Current smoking No 1.04(I.00-1.07) 1.20(I .0g-1.38) by th~ spous~ Yes l.Og(1.05-I .12) 1.20(I. t I-1.35) * Yc!~ - using data adjusted for covariatcs whcre possible, unadjusted data otherwise No - using data unadjusted for covariatcs where possible, adjusted data otherwise

"03-NOU-1997 4.2 GALLAHER CORPORATE AFFRS 0193283253R Seven studi~ provide |2 estimates of relative risk of IHD essocJatcd with workpl~,¢ exposure. None of these estimates is statistically significan( after adjustment forcovariates. Fixed-effectsmeta-~alysis ofthese statistically homogeneous estimates gives a relative risk of i .06 (0.95 to 1.19) unadjusted t'or covadatcs and 1.07 (0.96 to 1.I9) adjusted for covariates (Lee, 1997). By failing to conduct their ovm analyses of workplace exposure and restricting attention to spousal exposure Law, Mort.is and Weld give a false picture of the overall evidence. They elso give a false impression by citing an analysis by Wells (1995) submitted toOSHA which claimed a meta-analysis relative risk of 1.36 (1.08 to 1.7l). This is misleading as it: (i) does not cite comments by Lee (199:;) on Wells (1995) also submitted to OSHA which make it clear Wells' analysis was erroneous, and (ii) fails to make it clear the recta-analysis relative risk estimate would have been massively reduced by inclusion of data from Muscat and Wynder (! 995) and particularly from Steenland et ai (t996). P.0~/26 0 0

,03-NOU-1997 15:32 GALLAHER CORPORRTE AFFRS 0193283~532 P.07/26 14 SmokJr~ habit miscIassific~tion AIthou~hHackshaw, Law and Weld (1997)adjust spousal smoking risk estimates for lung cancer downward in an attempt to account for bias due to misclassification of smoking habits, Law, Morris and Weld (1997) rnak¢ no such adjustment when considering the evidence for [HD, arguing it will b¢ of negligible importance since the mlatlv¢ risk of IHD in smokers is so much smaller than that of lung cancer (about 2 cornp~ed ~o 20). This argument is incorrect. Whet affects the magnitude of bias is not the excess Hsk in ~, but the excess risk in misclassificd smokers. For lung cancer, FI~ckshaw# Law and Weld assume that the relative risk for misclassificd smokers will be .markedly less ihan the relative risk for all smokers, on the grounds that mi~¢lassifi¢d smokc~s tend to have. lower ¢otinine levels than average smokers, consisten[ with smoking less. This assumption may not bc um'casonable for lung cancer, but may be to~ly incorrect for heart disease. It is known that: (i) Hsk of heart disease death is high in patients with a previous myocardial infarction, (ii). patients= w~th a myocardial infection are us~ly advised by their doctors to give up.smokiZng, and (iii) miscl~ssification rates of smoking are particularly high in patients advised by their doctor to give up (Lc¢, 1988). It is reasonable tO. expect, therefore, that misclassJfied smokers will conlain a relatively high proportion of people with a previous myocardial infarction, and consequently be a relatively high risk group for [HD. R¢c, cnt results from a Danish prospective study ($uadicaRi ~/~z[, 1997) lend support to this possibility. In this study, self-reported smoking habits were recorded and serum samples.taken for cotinJn¢ deterrnination, the popul~tion then being followed-up fo~ eight years'. Cumulative heart disease incidence in self-reported nonsmokers wid~ cotinlne levels inconsistent with nonsmoking was 17.9%, based on t~vc cases. 3"his o o~ o3

~@3-NOU-19~? 15:32 GRLLRHER CORPORATE ~FFRS 15 incidence w~ not only higher th~n that in s~l f-repor',~ nonsmokcrs with cotininc levels below 100 ng/ml, 3.1% based on 43 cases, but was also higher than that in self-reported current smok~ w~t.h cotin~ne levels above 100 ng/ml, 4.3% based on 72 cruses. Though more ~ m'e ne~ed, [he much higher risk seen in {his sLudy {'or rniscl,',ssificd vs. non- rnisclassified smokers (relative Hsk 4.01, 95% CI 1.76 to 9.13) suggcsts that misc[assillcation bia~ might be at Icast ~s relevant for he.~rt disease zs ~t ~s t'or lung c4~Icer, Cbarly t'a/Jure properly to con.sid,~ smoking habit miscla.ssificadon is a m~.~or Hmit~,tJonol~e paper by L,~w, Morals ~nd Wald. P.08/26

~ ~03-NOU-1887 15:32 GALLAHER CORPORATE AFFRS @1932832532 P.@gx26 4.4 4.4. i 16 Evidence fi'om the ETS/heart dise~¢_studies themselves Although Law, Morris and V/old consider the possible magnitude of bias on theoretical grounds (se~ below) it is surprising flint they do not look in detail at the effect confounding adjustment had in the 19 epidcmiological studies they include in their mesa- analysis. Although many of these studies paid only limited attention to potential confounding vm-iables, with many not even t~Jng into account the cla~sicaJ coronary risk factors of" blood pressure, choleslerol and body m~s index, many of the studies did press.hi relative risk estimates before and after adjustment for age and v~rious other factor. The table overleaf summarizes the relevant data and shows the effect that adj~o'nenl for age, for [he o~hcr factors or for age and the other factors combined hnd on the ~e!ative. risk estimates. A striking feature of the data is how large and variable the effects of adjustment were. While Law, Morris and Wald are daim~ng that adjustment would only have a very modest effect on risk estimates, there were a considerable number of studies where adjustment decreased or increased relative r/sk estimates by a factor of 1.20 or more (highlighted in the table). In the two Chinese studies (He e¢ al, I989; He er al, 1994) adju.C.ment explained as much as $0% of the excess risk. : While the overall pattern of results is not clear, partly due to the diffi.cultics of separa.'ting effects of age adjustznent from effects of adjustment for other factors, and tartly due to variability in which other factors were considered, there is clearly a suggestion that confounding may be more important that Law, Morr/s and Wald suggest. They do note that relative risks adjusted and unadjusted for blood pressure, serum cholesterol, body mass index and a measure of social class were similar, but this conceals the fact that sp¢cific studies found that adjustment had quite iargc effect.s, more than Law. Morris and 9/aid suggest could possibly be due to confounding. 0 o~ O3 03 0 O~

~ "03-NOU-199T 15:33 G~LL~HER CORPORATE ~FFRS 01932832532 P.18x26 H!rzy~'la (1990) ' ~m'l~nd (198.~) ~d1~<i989) HumhleO990) ~h~n 0991) He ¢i Me,in C E C C C C C C C t2, 17 Relallve rbkS ^djumo ~ljusxr.d l'or ~ge corm.lares (K,) (Re) CRy) 1.16 3,51 2.70 2.~ 2.25 0.97 - 0.93 1.47 1.61 -. 3.52 I 1.15 !.3I 0.70 1.19 I.~ ~ 0.97 1.61 - 2.46 1.17 1.31 1.21 2.12 - !,~2 - !.~ I.? I 1.97 !.36 1.0~ - i.15 [.40 4.40 3.40 130 3,7~ Eff~! of adju stmenl For For a~¢ olhu ,lad othu (Kd~,) (X~X~) (R/R,) 1.[6 - ! .05 - 0.93 0.96 - 1,10 - 0.43 - !.14 o 1.70 1.19 - 0.93 - I I. ! 2 0.92 1 .~3 - 0,58 - 1,04 0.87 - 0.76 . 1.2~. - 0.77 - 0.96 - 0.94 Nero: Data Crom I.ee(1997). Bold values inflate adjustment affected risk u'pw+u'd or down,.v~d by • fnclor of 1.20 or more. r~3 o 0"~ ~0 0 ~0

~ "03-NOU-1997 4.4.2. 15:33 GRLLRHER CORPORRTE RFFR~ 81932832532 P.11/26 "Direct" cstimate~ of c0nfoundin~ Law, Morris and Na~d first ~mpt to cstimate ~e extcnt ~o which confounding by o~¢r ~sk factors ~t bi~ the ~ia~on ~een smo~ng estimate that confounding due to smoker/nonsmoker diffe~n~s in fruit and vegcmblc ~ption ~d in LDL cholc~crol would c~h ~ ~ ex~ss risk of3%, wi~ blood pre~¢ ~d o~r risk f~tors For IHD h~ving negligible conFo~ding effect. The conclusions for fi-uit and vegetable consumption arc based on an ~alysis reported in a pap¢~ that is "in press" and cannot be studied in detail. Jt is not made clear whether any adjustments havc bccn made for the fact that the reported relationship of diet • t~ disease (and consequently the estimated confounding effect) is likely to b¢ weaker than it actuldly is, due to the substantial errors inherent in estimating consumplion. Morn scri0usly, in view of the 250 or so risk factors that have been identified for~-- heart disease (KarmeI, 1987; Stokes, 1987; Hopkins and Williams, 1981), one must question whether Law, Morris and Wold have comprehensively considered the possible sources of confounding. As noted by Thornton et a! (1987) smokers have increased cxposur¢to very many lifestyI¢ risk factors. Based on. the smaller differences in fruit and vegetable consumption between nonsn~okers who do and do not live with a smoker than between nonsmokers and smokers, Law, Morris and Wold estimate confounding from this source will be less important for.passive San for act/re smokJng. This assumes that th~ association between diet ar~ ]HD is similar in non.smokers and in smokers, an assumption that has not been Considered. Just as when considering smoker/nonsmoker differences, the discussion regarding differences in relation to spousal smoking is limited to only a few of the risk factors identified for heart disease. It is difficult to accept that their analyses provide a r¢tbbl¢ indication of the true effect of confounding.

~03-NOU-199T 4.4.3 15:34 GALLAHER CORPORATE AFFRS 01932832532 19 ~[/Id.j~irn~tcs ofconfound~ne Law, Morris and Wold arc arguing, cssentiaJly, th.~t the obse~ incre~d IHD ~sk in smokers is p~y cause ~d eff~t ~nd p~ly due m confounding, ~d that a~cr giving up ~oking for m~y ye~s the in~cased risk duc to smo~ng is elimina~d d~e inc--due to ~nfo~ding remains. Bemuse the reladvc risk of he~ disease in long te~ ex-smokers ~ '~timated ~ only ! .06, ~ey suggc~ ~at ibis estimate se~ ~ upp~ limit to ~y eff~t of~nfounding. This argument would only have some credence if the distribution of hca,-t disease ~isk factors was similar in current smokers and cx-smokers and, within ex-smokcrs, was similar regard|ess of amount smoked. This is clearly not true. As Thornton eta/ (! 994) clcady showed, for many lifestyle Hsk factors, current smokers have the highest prevalence, ne'~er smokers the leasl and exosmokers intermediate, with [bc difference between ex-smoke~J and never smokers greatesl for shor~ term ex-smokers and least for tong term ex-smokcrs. Based on their results, any confounding effect for long term smokers would be only a fraction of the confounding effect for current smokers. To some extent Law, Morris and Waid recognize this point when they note that people who give up smoking may change their diet. But this is far From the whole story. Increasing i~gth ofex-smoking is significantly associated, according to Thornton et al (! 994), with higher social class, bet'zr education, higher income, working less in "dirty" • jobs, being more likely to do something to keep healthy, as well as numerous aspects of improvement in diet (including less fried foods, more cereal, more fi'uits, vegetables and P.12/26

" ~ 03-NOU-1997 4.5 15:34 GALLAHER CORPORATE RFFRS 81932832532 2O Law, Morris end Wald note that eigh~ studies found a significant (p<0.05) positive result, a result one would expect to see by ehan~, not in the/.9 studies they consider, but in 320 studies. They ~hen argue that it b implausible that then: should be ~s many as 301 unpublished studies, so that. publication bias cannot account for the Observed .association. Thc.r~ ~re two major weadmesses with this arBument. The first is that it ordy dens with the rather uninteresting hypothesis that publication bias ~x.otmts for all the observed associ~.ion. 'l"hJs is hardly relevant when the studies are likely to b~ affected by various other forms of bias, and does not argue against the possibility that the true association is in fact weber zb, n th~ 0bserved in published studies. The second is that it totally ignores the fact that exis6rtg studies (CPS-I and NMFS) have been omitted lYom analysis, although there is evidence that the relative risks from these studies are substantially less Ihan the calculated morn-analysis estimate. It is in fact difficult to understand how anyone could possibly try. to argue that publicatlon bias is not.an issue given thcir knowlcdg¢ ofth¢ existence of these studies and of various warnings in the literature about the likely bias from failing to consider their results (Lee. 1992: LeVois and Layard, 1995). P.13/26