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The composite RR is 1.17. *Data not available.t ڐ, with the ones selected for analysis in this report in boldface type. Table 55 lists the RRs and their confidence intervals, along with explanatory footnotes, and Table 56 provides information on source and place of exposure and on the adjusted analysis. Because most studies include spousal smoking, and interstudy comparisons may be useful, spousal smoking was the preferred ETS surrogate in all except for LAMW and SOBU. In LAMW, spousal smoking data are limited to cases with adenocarcinoma; in SOBU, the data for cohabitants are separate from data for spousal smoking, and much of the ETS exposure appears to result from the cohabitants. Only data for broader exposure to ETS than spousal smoking alone were collected in BUFF, CHAN, SVEN, and HOLE(Coh). After exposure source and place are taken into account in the choice of RR values in Table 56, an adjusted RR is considered preferable to a crude RR unless the study review in Section A.4 indicates a problem with the adjustment procedure. Of the 31 studies, 20 provide both an adjusted and crude RR, where the "adjusted estimate" is based on the author's use of a statistical procedure that takes potential confounding factors into account, usually by stratification or logistic regression. Based on the decision rule just described, our choice of RR is the smaller of the crude and adjusted values in 14 of the 20 studies providing both estimates. In several studies, RR values in addition to those shown in Table 56 might be considered (see Table 57x(x(X` hp x (#%'0*,.8135@8:<:4.2&&SHIM<1.08 < (0.70, 1.68)<&1.07 M<$(0.7, 1.67)<01.01><:2.8&&SOBU<  ă <1.57 <(1.13, 2.15) 1.00<92.81&&SVEN<1.26 < (0.65, 2.48)<&1.20 #<$(0.63, 2.36)<01.05<96.00&&TRIC<  ă <2.08 <(1.31, 3.29)?<$ ă<01.00 <92.81&&WU<1.41 < (0.63, 3.15)<&1.32 #<$(0.59, 2.93)<01.07<94.38&&WUWI<0.79 < (0.64, 0.98)<&0.78 #<$(0.63, 0.96)<01.01<92.24&&BUTL (Coh)<2.027ă < (0.48, 8.56)6ă<&2.01 #<$(0.61, 6.73)1.00><:4.0&&GARF (Coh)<1.177ă < (0.85, 1.61)6ă<&1.16 #<$(0.89, 1.52)<01.01<93.58&&HIRA (Coh)<1.38 < (1.03, 1.87)<&1.37 #<$(1.02, 1.86)<01.01<93.20&&HOLE (Coh)<1.997ă < (0.24, 16.7)6ă<&1.97 <$(0.34, 11.67)1.01><:4.2 1OR for casecontrol studies; RR for cohort studies. 2Adjusted OR in Table 55 is used unless the confidence interval is unknown or the study review (Appendix A) is critical of the method(s) used. 3Corrected (2) (estimate and confidence interval) equals uncorrected (1) times ratio [(2)/(1)]. All corrected 95% confidence intervals have been converted to 90% confidence intervals. 4Values shown are the lower of (calculated ratio, 1). Calculated ratios less than 1 are shown in parentheses. 5The crude OR for eversmokers in Table 55 is used in the calculations for the corrected value (Appendix B), when available. Eversmoker ORs for GARF, JANE, PERS, and SHIM are approximated from the data of other studies for suitable location and time period. The ever smoker ORs for BUTL(Coh) and (LEE) are based on data in Fraser et al. (1991) and Alderson et al. (1985), respectively. 695% confidence interval. 7Adjusted RR value in Table 55.Iڐ. In general, the biases are low in East Asia, or in any traditional society such as Greece, where female smoking prevalence is low and the female smoker risk is low. Some of the calculated biases are slightly less than unity when carried to three decimal places. This may result from the assumption in the calculations that there is no passive smoking effect on current smokers. 5.3. STATISTICAL INFERENCE 5.3.1. Introduction ČTable 596x(x(X` hp x (#%'0*,.8135@8:0.5*0.74(0.47, 1.17).@@.HKKOO200.430.060.161.54(0.98, 2.43).@@.HKLAMT450.73<0.01<0.011.64(1.21, 2.21).@@.HKLAMW150.39<0.01*2.51(1.49, 4.23).@@. HKALL14܃<0.01܃1.48(1.21, 1.81) .@@.܃܃܃܃.@@.JapanAKIB150.420.050.031.50(1.00, 2.50)..JapanHIRA (Coh)350.750.04<0.011.37(1.02, 1.86).@@.JapanINOU30.170.07<0.032.55(0.90, 7.20).@@.JapanSHIM160.3770.38*1.07(0.70, 1.67).@@.JapanSOBU300.660.01*1.57(1.13, 2.15).@@. JapanALL19܃<0.01܃1.41(1.18, 1.69) .@@.܃܃܃܃.@@.USABROW10.150.28*1.50(0.48, 4.72).@@.USABUFF30.17>0.5*0.68(0.32, 1.41)..USABUTL (Coh)10.180.17*2.01(0.61, 6.73).@@.USACORR30.220.100.011.89(0.85, 4.14).@@.USAFONT8350.930.030.041.28(1.03, 1.60).88.USAGARF150.6070.12<0.021.27(0.91, 1.79) ..܃ `x-(continued on the following page)6ڐx(x(X` hp x (#%'0*,.8135@8:0.5*0.79(0.52, 1.17).@@.USAKABA20.177>0.5*0.73(0.27, 1.89).@@.USAWU30.210.29 < *1.32(0.59, 2.93).@@. USAALL34܃0.02܃1.19(1.04, 1.35) .@@.܃܃܃܃..ScotlandHOLE (Coh)100 0.090.26*1.97(0.34, 11.67).@@.Eng./WalesLEE1000.200.50*1.01(0.47, 2.15).@@.SwedenPERS680.4570.270.121.17(0.75, 1.87).@@.SwedenSVEN320.240.31*1.20(0.63, 2.36).@@. W. Europe  ALL  5 ܃ 0.22 ܃ 1.17  (0.84, 1.62) .@@.܃܃܃܃.PP.#&m P7&P#ChinaGAO280.660.180.291.19(0.87, 1.62).PP.ChinaGENG80.320.01<0.052.16(1.21, 3.84).PP.ChinaLIU40.18>0.5*0.77(0.35, 1.68).PP.ChinaWUWI600.897>0.5*0.78(0.63, 0.96).. ChinaALL22܃>0.5܃0.95(0.81, 1.12)  1Misclassification is discussed in Section 5.2.2 and Appendix B. 2A study's relative weight (wt) is 1/var (log(OR)), divided by the sum of those terms for all studies included, times 100 (to express as a percentage). 3A priori probability of significant (p < 0.05) test of effect when true relative risk is 1.5. 4Onesided pvalue for test of RR = 1 versus RR > 1. 5Pvalue for upward trend. Pvalues from studies reporting only the significance level for trend were halved to reflect a onesided alternative, i.e., upward trend. 6Adjusted for smoker misclassification. OR used for casecontrol studies; RR for cohort studies. 7Calculated for matched study design. 8For population control group only, all cases. *Data not available; ns = not significant.ڐ lists the values of several statistical measures for the effect of spousal smoking by study (see boldface entries in Table 56 for details). Their meanings will be described before proceeding to interpretation of the data, even though the concepts discussed may be familiar to most readers. The pvalues refer to a test for effect and a test for trend. In the former, the null hypothesis of no association (referred to as "no effect" of ETS exposure on lung cancer risk) is tested against the alternative of a positive association. The test for trend applies to a null hypothesis of no association between RR and exposure level against the alternative of a positive association. When data are available on more than two levels of intensity or duration of ETS exposure, typically in terms of the husband's smoking habit (e.g., cig./day or years of smoking), then a test for trend is a useful supplement in testing for an effect, as well as indicating whether a doseresponse relationship is likely. The entries under "power" in Table 59 are calculated for the study's ability to detect a true relative risk of 1.5 and a decision rule to reject the null hypothesis of no effect when p < 0.05 (see Dupont and Plummer [1990] for methods to calculate power). The power is the estimated probability that the null hypothesis would be rejected if the true relative risk is 1.5 (i.e., that the correct decision would result; the power would be larger if the true relative risk exceeds 1.5). If the estimates of power for the U.S. studies in Table 59 are used for illustration, it can be seen that the estimated probability that a study would fail to detect a true relative risk of 1.5 (equal to 1  Power, the probability of a Type II error [discussed in the next paragraph] when the true relative risk is 1.5) is as follows: FONT, 0.07; GARF(Coh), 0.08; GARF, 0.40; JANE, 0.56; BUFF, 0.83; CORR, 0.78; WU, 0.79; HUMB, 0.80; KABA, 0.83; BUTL(Coh), 0.82; and BROW, 0.85. Thus, 7 of the 11 U.S. studies have only about a 20% chance of detecting a true relative risk as low as 1.5 when taken alone. Sources of bias effectively alter the power in the same direction as the bias (e.g., a downward bias in RR decreases the power). Of the potential sources of bias discussed by study in Section A.4, the predominant direction of influence on the observed RR, when identifiable, appears to be in the direction of unity, thus affecting power adversely. The RRs already have been reduced to adjust for smoker misclassification, the only systematic source of upward bias that has been established. Studies of all sizes, large and small, are equally likely to make a false conclusion if ETS is not associated with lung cancer risk (Type I error). However, smaller studies are less likely to detect a real association when there is one (Type II error). This imbalance comes from using the significance level of the test statistic to determine whether to reject the null hypothesis. If the decision rule is to reject the hypothesis when the pvalue is smaller than some prescribed value (e.g., 0.05), then the Type I error rate is 0.05, but the Type II error rate increases as study size decreases. When a study with low power fails to reject the null hypothesis of no effect, it is not very informative because that outcome may be nearly as likely when the null hypothesis is false as when it is true. When detection of a small relative risk is consequential, pooling informational content of suitably chosen studies empowers the application of statistical methods. The heading in Table 59 that remains to be addressed is "relative weight," to be referred to simply as "weight." When the estimates of relative risk from selected studies are combined, as for studies within the same country as shown in the table, the logarithms of the RRs are weighted inversely proportional to their variances (see Appendix D and footnote 2 of Table 5-9). These relative weights are expressed as percentages summing to 100 for each country in Table 59. Study weight and power are positively associated, which is explained by the significant role of study size to both. Consequently, studies weighted most heavily (because the standard errors of the RRs are low) also tend to be the ones with the highest power (most likely to detect an effect when present). 5.3.2. Analysis of Data by Study and Country 5.3.2.1. Tests for Association  The pvalues of the test statistics for the hypothesis of no effect (i.e., RR = 1) are shown in Table 59. Values of the test statistics (the standardized log odds ratio; see Appendix D) are plotted in Figure 51:x(x(X` hp x (#%'0*,.8135@8: 1. 5Adjusted for smoker misclassification. OR used for casecontrol studies; RR for cohort studies. 6Values may differ from those of Table 511, where confidence intervals are shown as they appear in the source. In Table 511, the RR and confidence interval are not corrected for smoker misclassification, as in this table, and most of the confidence intervals are 95% instead of 90%. 7Value shown is for all cell types with the two control groups combined. For adenocarcinoma cases only, the RR is 1.68 with C.I. = 0.81, 3.46. 8Relative weight assumed to be the same as for CORR, based on the outcome in Table 59. *Data not available.ڐ. As indicated in the table, exposurelevel data are available in 17 studies. The definitions of highest exposure category, shown next to the study name in the table, vary widely between studies. Crude RR estimates adjusted for smoker misclassification (see Section 5.2 and Appendix B) are used in this section rather than the estimates adjusted for modifying factors within the studies, because the latter are available by exposure level for only a limited number of studies. Several observations are apparent from Table 510. First, every one of the 17 individual studies shows increased risk at the highest exposure level, even after adjusting for smoker misclassification. Second, 9 of the 16 comparisons for which sufficient data are available are statistically significant (p  0.05), despite most having very low statistical power. Third, the RR estimates pooled within countries are each statistically significant with p  0.02. Although the RR estimates within a country are pooled across different definitions of highest exposure, which somewhat limits their interpretation and practical value, it is apparent that these RRs are considerably higher than the values observed for the dichotomous data (Table 59). The RR estimates pooled by country vary from a low of 1.38 (p = 0.005) for the United States to a high of 3.11 (p = 0.02) for Western Europe, which contains only one study. Finally, the overall pooled estimate of 1.81 for the highest exposure groups from all 17 studies is highly statistically significant (p < 0.000001). These results are consistent with the statistical evidence presented in Section 5.3.2 for an association between ETS exposure and lung cancer. In fact, increased risks are found for the highest exposure groups without exception. Furthermore, the RR estimates pooled within countries are all statistically significant and range from 1.38 to 3.11, even after adjustment for smoker misclassification. The consistency of these highest exposure results cannot be accounted for by chance, and the stronger associations detected for the highest exposure groups across all countries further reduce the likelihood that bias or confounding could explain the observed relationship between ETS and lung cancer. In addition, with the exception of Western Europe, which contains only one lowpower study in this analysis, the pooled RR estimates from other, more "traditional" countries are all appreciably higher than that from the United States. It is likely that these differences are at least partially a result of higher background (nonspousal) ETS exposures to the allegedly "unexposed" group in the United States. Again, this highlights the importance of accounting for ETS exposures from sources other than spousal smoking. An adjustment for background ETS exposures is made in Chapter 6, for the estimation of population risk for the United States. 5.3.3.3. Tests for Trend In this section, exposureresponse data from the studies providing data by exposure level are tested for upward trend. An exposureresponse relationship provides strong support for a causal association (see Section 5.3.3.1).Table 511x(x(X` hp x (#%'0*,.8135@8:301.00 1.19 1.14 1.25 (0.88, 1.61) (0.82, 1.59) (0.91, 1.72)0.07*``*FONT7 (years)* * * ** * * *0 115 1630 >301.00 1.33 1.40 1.43 (0.93, 1.89) (0.96, 2.05) (0.99, 2.09)0.02**FONT6 (packyrs.)* * * * ** * * * *܃ 0<15 1539 4079 801.00 0.96 1.13 1.25 1.33 (0.72, 1.29) (0.81, 1.59) (0.86, 1.81) (0.68, 2.58)0.04**FONT7 (packyrs.)* * * * ** * * * *܃ 0<15 1539 4079 801.00 1.03 1.26 1.49 1.70 (0.73, 1.46) (0.85, 1.87) (0.98, 2.27) (0.82, 3.49)0.01*``*GAO (tot. yrs.)899 93 107 7657 63 78 48019 2029 3039 401.0 1.1 1.3 1.7 (0.7, 1.8) (0.8, 2.1) (1.0, 2.9)0.29 *``*GARF (cig./day)44 29 17 26157 90 56 440 19 1019 201.00 1.15 1.08 2.11 (0.8, 1.6) (0.8, 1.5) (1.1, 4.0)<0.02 *DD*GENG (cig./day)* * * * * * * *0 19 1019 201.00 1.40 1.97 2.76 (1.1, 1.8) (1.4, 2.7) (1.9, 4.1)<0.059 `x.(continued on the following page)ڐx(x(X` hp x (#%'0*,.8135@8:@@@P>@@@P Study Trend test results EEEUEEEUIntensity (cig./day)Duration (total years)Cumulative (packyears)2@@AKIB0.030.24*@@CORR**0.01FONT* *0.073 <0.0240.04 <0.01@@GAO*0.29*@@GARF<0.02**@@GENG<0.055<0.055*@@HUMBns**@@INOU<0.03**@@JANE *6**@@KALA0.080.04*@@KOO0.16**LAMT<0.01 <0.014**@@PERS0.12**@@TRIC<0.01**@@WU* *6*@@GARF(Coh) *6**88HIRA(Coh)<0.01**  1Detailed data presented in Table 511. 2A "packyear" is equivalent to one pack/day for 1 year. 3All cell types. 4Adenocarcinoma only. 5See footnote 9 in Table 511. 6Trend results presented without pvalues or raw datasee Table 511. *Data not available; ns = not significant.h ڐ summarizes the pvalues of the trend tests for the various ETS exposure measures from the studies presented in Table 511. The exposure measure most commonly used was intensity of spousal smoking. Eight of the twelve studies that reported exposureresponse data based on cigarettes per day showed statistical significance at the p < 0.05 level for the trend test. Again, the probability of this many statistically significant results occurring by chance in this number of studies is negligible (p < 107). The trend test results for the other exposure measures were consistent, in general, with those based on cigarettes per day (three of six studies using total years of exposure were significant, as were two of two studies using packyears). Overall, 10 of the 14 studies with sufficient exposureresponse data show statistically significant trends for one or more exposure measures. No possible confounder has been hypothesized that could explain the increasing incidence of lung cancer with increasing exposure to ETS in so many independent studies from different countries. By country, the number of studies with significant results for upward trend is as follows: China, 1 of 2; Greece, 2 of 2; Hong Kong, 1 of 2; Japan, 3 of 3; Sweden, 0 of 1; and United States, 3 of 4. Of particular interest, two of the U.S. studies, GARF and CORR, are statistically significant for a test of trend, providing evidence for an association between ETS exposure and lung cancer even though neither was significant in a test for effect. In both cases, this occurs because the data supporting an increase in RR are largely at the highest exposure level. It appears that relatively high exposure levels are necessary to observe an effect in the United States, as would be expected if spousal smoking is a weaker surrogate for total ETS exposure in this country. The U.S. study by Fontham et al. (1991), a wellconducted study and the largest casecontrol study of ETS and lung cancer to date, with the greatest power of all the U.S. studies to detect an effect, was statistically significant with a pvalue of 0.04 for the trend test with packyears as the exposure measure. When the analysis was restricted to adenocarcinomas (the majority of the cases), tests for trend were statistically significant by both years (p = 0.02) and packyears (p= 0.01). 5.3.4. Conclusions Two types of tests have been conducted: (1) a test for effect, wherein subjects must be classified as exposed or unexposed to ETS, generally according to whether the husband is a smoker or not, and (2) a trend test, for which exposed subjects are further categorized by some level of exposure, such as the number of cigarettes smoked per day by the husband, duration of smoking, or total number of packs smoked. Results are summarized in Table 513 x(x(X` hp x (#%'0*,.8135@8:0.50""Hong KongKOO0.43Effect Trend0.06 0.16""Hong Kong LAMT 0.73 Effect Trend  <0.01 <0.01 "@@"Hong Kong  LAMW 0.39 Effect  <0.01 "@@"܃""Japan AKIB 0.42 Effect Trend  0.05 0.03 ""Japan HIRA(Coh) 0.75 Effect Trend  0.04 <0.01 ""Japan INOU 0.17 Effect Trend 0.07 (0.05)3 0.03 "@@"JapanSHIM0.37Effect0.38"@@"Japan SOBU 0.66 Effect  0.01 "@@"܃"@@"United StatesBROW0.15Effect0.28"@@"United StatesBUFF0.17Effect>0.50"@@"United StatesBUTL(Coh)0.18Effect0.17""United States CORR 0.22Effect Trend0.10 (0.005)3 0.01 ""United States FONT 0.93 Effect Trend  0.034 0.044 ""United States GARF 0.60 Effect Trend 0.12 (0.01)3 <0.02 "@@"United StatesGARF(Coh)0.92Effect0.18"88" `Lx-(continued on the following page) ڐx x X` hp x (#%'0*,.8135@8:0.50"@@"United StatesKABA0.17Effect>0.50"@@"United StatesWU0.21Effect0.29"@@"܃"@@"W. Europe܃"@@"ScotlandHole(Coh)0.09Effect0.26"@@"EnglandLEE0.20Effect0.50""Sweden PERS 0.45 Effect Trend0.27 (0.02)3 0.12"@@"SwedenSVEN0.24Effect0.31"@@"܃""China GAO 0.66 Effect Trend0.18 (0.02)3 0.29""China GENG 0.32 Effect Trend  0.01 <0.05 "@@"ChinaLIU0.18Effect>0.50"88"China WUWI0.89Effect>0.50 1Test for effectH0: no increase in lung cancer incidence in neversmokers exposed to spousal ETS; HA: an increase. Test for trendH0: no increase in lung cancer incidence as exposure to spousal ETS increases; HA: an increase. Pvalues less than 0.05 are in boldface. 2Smallest pvalue is used when there is more than one test for trend; ns = not significant. 3Pvalue in parentheses applies to test for effect at highest exposure only (see text). 4For all cell types. Pvalues for adenocarcinoma alone were smaller. ڐ, with countries in the same order as in Table 59. Studies are noted in boldface if the test of effect or the trend test is significant at 0.05 (onetailed) or if, as in PERS and GAO, only the odds ratio at the highest exposure is significant. In 8 of the 11 studies in Greece, Hong Kong, or Japan, at least one of the tests is significant at 0.05. For the United States and Western Europe, 4 of the 15 studies are significant at 0.05 for at least one test. For the studies within the first group of countries (Greece, Hong Kong, and Japan), the median power is 0.43, and only 1 of the 10 studies (10%) has power less than 0.25 (INOU). In contrast, the median power for the United States and Western Europe together is 0.21, and 10 of the 15 studies (67%) have power less than 0.25. In a small study, significance is meaningful, but nonsignificance is not very informative because there is little chance of detecting an effect when there is one. Consequently, there are several studies in the United StatesWestern Europe group that provide very little information. Two of the four studies in China are significant at the 0.05 level for at least one test. The two nonsignificant studies in China (LIU and WUWI) are not very informative on ETS for reasons previously described (see Section 5.3.2.1). For the U.S. and Western Europe studies, 3 of the 5 with power greater than 0.25 are shown in boldface (FONT, GARF, and PERS), indicating at least suggestive evidence of an association between ETS and lung cancer, compared with only 1 of 10 with power under 0.25 (CORR). All three of the higher power studies are significant for effect (PERS and GARF are significant at the highest exposure only) and two (FONT and GARF) are also significant for trend. CORR is significant for trend and for effect at the highest exposure level. Overall, the evidence of an association in the United States and Western Europe is strengthened by the tests at the highest exposure levels and by the tests for trend. To summarize, the results of the several different analyses in this section provide substantial evidence that exposure to ETS from spousal smoking is associated with increased lung cancer mortality. The evidence is strongest in Greece, Hong Kong, Japan, and the United States. The evidence for Western Europe appears similar to that in the United States, but there are far fewer studies. (The usefulness of statistical information from studies in China is quite limited, so no conclusions are drawn from the studies there.) The evidence from the individual studies, without pooling within each country, is also conclusive of an association. Adjustment, on an individual study basis, for potential bias due to smoker misclassification results in slightly lower relative risk estimates but does not affect the overall conclusions. The results based on either the test for effect or the test for trend cannot be attributed to chance alone. Tests for effect, tests at the highest exposure levels, and tests for trend jointly support the conclusion of an association between ETS and lung cancer in neversmokers. 5.4. STUDY RESULTS ON FACTORS THAT MAY AFFECT LUNG CANCER RISK 5.4.1. Introduction 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. Potential sources of bias and confounding must still be considered to determine whether they can explain the observed increases. While the exposureresponse relationships reviewed in Section 5.3.3.3 generally reduce the likelihood of bias and confounding accounting for the observed associations, this section focuses on specific factors that may bias or modify the lung cancer results. Validity is the most relevant concern for hazard identification. Generalizability of results to the national population (depending on "representativeness" of the sample population, treated in the text) is important for the characterization of population risk, but no more so than validity. As stated by Breslow and Day (1980), "In an analysis, the basic questions to consider are the degree of association between risk for disease and the factors under study, the extent to which the observed associations may result from bias, confounding and/or chance, and the extent to which they may be described as causal." Whereas Section 5.3 examined the epidemiologic data by individual study and by pooling results by country, this section considers potential sources of bias and confounding and their implications for interpretation of study results. As indicated in the brief review of the meanings of bias and confounding at the end of this section, confounding arises from the characteristics of the sample population, whereas bias is the result of individual study features involving design, data collection, or data analysis. Section 5.4.2 briefly reviews the evidence on nonETS risk factors and modifiers of lung cancer incidence that appears in the 30 epidemiologic studies (not counting KATA) reviewed for this report. None of the factors has been established as a confounder of ETS, which would require demonstrating that the factor causes lung cancer and is correlated with ETS exposure (specifically, spousal smoking to affect the analysis in this report). Our objective is to consider the influence of sources of uncertainty on the statistical measures summarized in Table 513, although there are limitations to such an endeavor. For example, not controlling for a factor such as age in the statistical analysis, which should be done whether or not the study design is matched on age, may require reanalyzing data not included in the study report. Potential sources of bias are just thatpotentialĩand their actual effect may be impossible to evaluate (e.g., selection bias in casecontrol studies). Although numerous questions of interest cannot be answered unequivocally, or even without a measure of subjective judgment, it is nevertheless worthwhile to consider issues that may affect interpretation of the quantitative results. The issues of concern are largely those of epidemiologic investigations in general that motivate the conscientious investigator to implement sound methodology. Statistical uncertainty aside, the outcomes of studies that fare well under close examination inspire more confidence and thus deserve greater emphasis than those that do poorly. Preliminary to the next sections, some relevant notes on epidemiologic concepts are excerpted from two IARC volumes entitled Statistical Methods in Cancer Research (Breslow and Day, 1980, 1987), dealing with casecontrol and cohort studies, respectively, which are excellent references. In the interest of brevity, an assortment of relevant passages is simply quoted directly from several locations in the references (page numbers and quotation marks have been omitted to improve readability). Some readers may wish to skip to the next section; those interested in a more fluid, cogent, and thorough presentation are referred to the references. XffffBias and confounding. The concepts of bias and confounding are most easily understood in the context of cohort studies, and how casecontrol studies relate to them. Confounding is intimately connected to the concept of causality. In a cohort study, if some exposure E is associated with disease status, then the incidence of the disease varies among the strata defined by different levels of E. If these differences in incidence are caused (partially) by some other factor C, then we say that C has (partially) confounded the association between E and the disease. If C is not causally related to disease, then the differences in incidence cannot be caused by C, thus C does not confound the disease/exposure association. fffConfounding in a casecontrol study has the same basis as in a cohort study. . . and cannot normally be removed by appropriate study design alone. An essential part of the analysis is an examination of possible confounding effects and how they may be controlled. fffBias in a casecontrol study, by contrast, [generally] arises from the differences in design between casecontrol and cohort studies. In a cohort study, information is obtained on exposures before disease status is determined, and all cases of disease arising in a given time period should be ascertained. Information on exposure from cases and controls is therefore comparable, and unbiased estimates of the incidence rates in the different subpopulations can be constructed. In casecontrol studies, however, information on exposure is normally obtained after disease status is established, and the cases and controls represent samples from the total. Biased estimates of incidence ratios will result if the selection processes leading to inclusion of cases and controls in the study are different (selection bias) or if exposure information is not obtained in a comparable manner from the two groups, for example, because of differences in response to a questionnaire (recall bias). Bias is thus a consequence of the study design, and the design should be directed towards eliminating it. The effects of bias are often difficult to control in the analysis, although they will sometimes resemble confounding effects and can be treated accordingly. fffTo summarize, confounding reflects the causal association between variables in the population under study, and will manifest itself similarly in both cohort and casecontrol studies. Bias, by contrast, is not a property of the underlying population. It results from inadequacies in the design of casecontrol studies, either in the selection of cases or controls or from the manner in which the data are acquired. fffOn prospective cohort studies. One of the advantages of cohort studies over casecontrol studies is that information on exposure is obtained before disease status is ascertained. One can therefore have considerable confidence that errors in measurement are the same for individuals who become cases of the disease of interest, and the remainder of the cohort. The complexities possible in retrospective casecontrol studies because of differences in recall between cases and controls do not apply. [Regarding the success of a cohort study, the] followup over time . . . is the essential feature. . . . The success with which the followup is achieved is probably the basic measure of the quality of the study. If a substantial proportion of the cohort is lost to followup, the validity of the study's conclusions is seriously called into question. fffOn casecontrol studies. Despite its practicality, the casecontrol study is not simplistic and it cannot be done well without considerable planning. Indeed, a casecontrol study is perhaps the most challenging to design and conduct in such a way that bias is avoided. Our limited understanding of this difficult study design and its many subtleties should serve as a warningthese studies must be designed and analyzed carefully with a thorough appreciation of their difficulties. This warning should also be heeded by the many critics of the casecontrol design. General criticisms of the design itself too often reflect a lack of appreciation of the same complexities which make these studies difficult to perform properly. fffThe two major areas where a casecontrol study presents difficulties are in the selection of a control group, and in dealing with confounding and interaction as part of the analysis. . . these studies are highly susceptible to bias, especially selection bias which creates noncomparability between cases and controls. The problem of selection bias is the most serious potential problem in casecontrol studies. . . . Other kinds of bias, especially that resulting from noncomparable information from cases and controls are also potentially serious; the most common of these is recall . . . bias which may result because cases tend to consider more carefully than do controls the questions they are asked or because the cases have been considering what might have caused their cancer. X` hp x (#%'0*,.8135@8: 4; neversmoker). HIRA(Coh) did not present findings for husband's occupation as a risk factor independently but reported that adjustment for this factor did not alter the study's ETS results. Few studies attempted to adjust ETS findings for occupational factorsSHIM found only modest effects of such adjustment for occupational metal exposure, despite an apparent strong independent effect for this factor, and GENG found only minimal effect of occupational exposure on active smoking results but did no adjustment of ETS results. Overall, multiple comparisons, other factors (e.g., socioeconomic status, age), and the rarity of most specific occupational exposure sources probably account for the inconsistent role of occupation in these studies. 5.4.7. Dietary Factors Investigations related to diet have been reported in nine of the ETS studies, with mixed outcomes. The fundamental difficulty lies in obtaining accurate individual values for key nutrients of interest, such as carotene. The relatively modest size of most ETS study populations adds further uncertainty in attempts to detect and assess any dietary effect that, if present, is likely to be small. In those studies where dietary data were collected and adjusted for in the analysis of ETS, diet has had no significant effect. Nevertheless, diet has received attention in the literature as a possible explanatory factor in the observed association between ETS exposure and lung cancer occurrence (e.g., Koo, 1988; Koo et al., 1988; Sidney et al., 1989; Butler, 1990, 1991; Marchand et al., 1991); therefore, a more detailed and specific discussion is provided in this section. Diet is of interest for a potential protective effect against lung cancer. If nonsmokers unexposed to passive smoke have a lower incidence of spontaneous (unrelated to tobacco smoke) lung cancer incidence due to a protective diet, then the effect would be upward bias in the RR for ETS. However, for diet to explain fully the significant association of ETS exposure in Greece, Hong Kong, Japan, and the United States, which differ by diet as well as other lifestyle characteristics, it would need to be shown that in each country: (1) there is a diet protective against lung cancer from ETS exposure, (2) diet is inversely associated with ETS exposure, and (3) the association is strong enough to produce the observed relationship between ETS and lung cancer. Diet may modify the magnitude of any lung cancer risk from ETS (conceivably increase or decrease risk, depending on dietary components), but that would not affect whether ETS is a lung carcinogen. The literature on the effect of diet on lung cancer is not consistent or conclusive, but taken altogether there may be a protective effect from a diet high in carotene, vegetables, and possibly fruits. Also, there is some evidence that low consumption of these substances may correlate with increased ETS exposure, although not necessarily for all study areas. The calculations made by Marchand et al. (1991) and Butler (1990, 1991) are largely conjectural, being based only on assumed data. Therefore, we examined the passive smoking studies themselves for empirical evidence on the effect of diet and whether it may affect ETS results. It was found that nine of the studies have data on diet, although only five of them use a form of analysis that assesses the impact of diet on the ETS association. None of those five studiesCORR, HIRA(Coh), KALA, SHIM, and SVENfound that diet made a significant difference. In the four studies where data on diet were collected but not controlled for in the analysis of ETS, three (GAO, KOO, and WUWI) are from East Asia and one (WU) is from the United States. Koo (1988), who found strong protective effects for a number of foods, has been one of the main proponents of the idea that diet may explain the passive smoking lung cancer effect. To our knowledge, however, she has not published a calculation examining that conjecture in her own study where data were collected on ETS subjects. In WU, a protective effect of carotene was found, but the data include a high percentage of smokers (80% of the cases for adenocarcinoma, 86% for squamous cell), and the number of neversmokers is small. In recent correspondence concerning the large FONT study, its authors state that "mean daily intake of betacarotene does not significantly differ between study subjects whose spouse smoked and those whose spouse never smoked" (Fontham et al., 1992). The equivocal state of the literature regarding the effect of diet on lung cancer is also apparent in the nine ETS studies that include dietary factors, summarized in Table 515x(x(X` hp x (#%'0*,.8135@8: