Document gD0moJ1qGYeNLnBeeYnJ67MO9

PLAINTIFF'S EXHIBIT AL-1222 ORIGINAL ARTICLES Scand } work environ health 8 0982) 153--158 Occupational mortality studies Principles of validity by Jung-Der Wang, MD, Olli S Miettinen, MD, PhD' WANG J-D, MIETTINEN OS. Occupational mortality studies: Principles of validity. Scand j work environ health 8 (1982) 153--158. Two common practices of occupational mortality studies have no model in experimentation: (a) the use of the "general popu lation" as a reference population and (b) the use of the total number of deaths as a surrogate for the population-time of follow-up. The former tends not to secure validity in terms of (i) comparability of effects, ie, identity of the extraneous effects of the compared experiences; (ii) comparability of populations, ie, absen.ce of Intract able confounding; and (iii) comparability of information, ie. Identity of the certification of deaths from the illness of interest for the contrasted populations. The use of a carefully selected, occupational reference population is necessary for all three types of comparability. When deaths from other (auxiliary) diseases are used to estimate the relative magnitudes of the compared populations, careful selec tivity is again called for. With respect to auxiliary causes of death, also, the com pared occupational populations must satisfy all three aspects of comparability, with the added requirement that the exposure under study have no effect The "healthy worker effect" is the result of failure to use comparable reference populations in occu pational mortality studies. Key terms: epidemiologic methods, statistics. In occupational mortality studies it is commonplace to compare the mortality of a population in a particular occupation with that of the "general population." The former is generally found to- be lower than the latter, and the difference is referred to as the "healthy worker effect" (16). If therapeutic research were con ducted in an analogous manner, treated patients would be compared with the 'general population" for any criterion of outcome. Experience would show that the treated group usually has a worse outcome than the reference population, and the difference might be referred to as the "sick patient effect." 1 Departments of Physiology, Epidemiology, and Biostatistics. School of Public Health. Harvard University, Boston, Massachusetts, United States. Keprint requests to: Prof OS Miettinen, Depart ment of Epidemiology, Harvard School of Public Health, 677 Huntington Avenue. Boston. MA 02115, USA. When the size of the occupational popu lation under study is unknown, it is cus tomary to compare the proportions of deaths of interest among all deaths (26). For this practice the counterpart in clinical trials would be the comparison of treatment groups in terms of the proportion of events of interest among all events within the treatment groups. It is evident that these common practices in occupational mor tality research are far removed from the experimental paradigm advocated for nonexperimental research by AB Hill (12), among others. In this paper we have attempted to de lineate the implications of the experi mental model for validity in occupational mortality studies. In particular, our con cern is to put forth some key principles of validity for forming population contrast, as well as for coping with the common lack of direct "denominator data." We have also discussed the "healthy worker effect" as a manifestation of the violation 0355-3140'82/030153-06USD1.75 752463 0041 v- of one of the principles of validity that we advocate. Object of study Meaningful discussion of validity in occu pational mortality (or any other type of) research presupposes keen appreciation of the nature of the object of study. There is little scientific point in knowing the mor tality from any disease Y in any occupa tion X in an absolute sense. Nor is there any intrinsic scientific interest in the relative mortality between occupation X and the "general population," even after adjustments for differences in distributions by age and gender. Such contrast is of interest only insofar as it addresses, in some sense, the effect of occupation X on mortality from disease Yl What might properly be meant by such an effect? The meaning might be thought to be the difference in mortality (from disease Y) that results from being or not being in occupation X. However, the difference depends on what the unspecified alternative to occupation X actually is. Without any explicit alternative such a concept of effect is of no scientific interest. While the alternative might be iden tifiable, the usual meaning of the effect of occupation X is that of the effect of a particular hazard or exposure (whether it be chemical, physical, psychological, or whatever) occurring in the occupation in question. This conceptualization of an occupational effect is analogous to the meaning of the effect of a drug regimen in a typical clinical trial, the usual con cern involving the effect of the drug itself ps distinct from its concomitants in the administration of the treatment. Thus the object of an occupational mortality study cannot be \he effects of, say, chemical manufacturing, copper smelting, or coke producing, but it can be -- and it has been -- the effect of occupational exposure to benzene (21), arsenic (1), or coal tar pitch volatiles (15). Only the study of the effects of exposure(s) provides the basis for hygienic improvements and standards. In terms of thinking of an epidemiologic study as addressing an occurrence relation (17). the object in any occupational mor tality study is the relation of a chosen parameter (incidence density, say) of the occurrence of the deaths of interest (due to a particular disease) to occupation -- given that the relation reflects the effect of interest, as already discussed. Thus an early concern of study design is to define the compared categories ot the determi nant -- the occupational contrast -- m conceptual terms. For this purpose two, already emphasized principles are im portant: first, that the determinant is to be thought of as an occupational exposure rather than as an occupation per se and, second, that the empirical relation is of interest only insofar as it can be inter preted in causal terms. Validity of occupational contrast The contrast of interest in conceptual terms having been defined, the next task is to give it an operational specification. For this purpose the validity concerns have to do with the attainment of the comparability of tlie compared occupation^ as regards (i) their respecUve effects, (u) the populations representing them, and (iii) the accuracy of information**on mortality (from the disease at issue) between Comparability of effects In order for an occupational contrast to reflect the effect of interest, even in a randomized experiment, the following conditions should be met: (i) the index occupation must indeed represent the ex posure; (ii) the reference occupation(s) must represent a lesser exposure than the index occupation, if not total nonexposure: and (iii) apart from the effect of the expo sure at issue, ie, on the "null hypothesis," the compared occupations must have identical effects on mortality from the disease ai issue. The last of these conditions is the counterpart of the therapeutic trial requirements that (i) the "placebo" drug or "sham" operation have no effect of its own and (ii) all extraneous aspects of the treatments in the index and reference groups have, in the aggregate, identical effects on the criterion of outcome. Example 1. Doll (7) studied the risks of lung and nasal cancers in relation to nickel expo sure (conceptually) by contrasting nickel re- 154 fining to steel making, coal mining, and all other occupations (operationally). The first two of the three needed conditions were readily satisfied, but the third leaves some un certainty, as is usual. The contrast of nickel the compared populations are defined so that such differential selectivity of mem bership does not occur between them, then they are comparable. detinea reierence occupation, ana it is aniicult for both investigators and readers to judge. As was already noted, the formulation of the occupational contrast is a matter of design ing the scale of the determinant in the oc currence relation that the study is to yield. It deserves careful note that the index occupa tion (representing the exposure) is compared with expressly selected reference occupations, ie, with only a subcategory of nonexposure that Is comparable in ellect with tne occupation under study. Example 2. Recall example 1 concerning lung cancer mortality in relation to nickel exposure. Even though employees might enter or leave the three occupational populations differen tially according to work preference, economic incentives, physical strength, training back ground, findings in preemployment physical examinations, medical surveillance, health in surance. etc, these factors are unlikely to have any appreciable relation to the risk of death from lung cancer. Thus they are unlikely to jeopardize the comparability of the index and reference populations -- conditional on age, gender, and calender time, which were con Comparability of populations trolled in the analysis. This comparability-of-populatlons principle for the design of the study base illustrates Given an occupational contrast with com again how the exposed are not to be com parable effects, there is a need to form a pared with the nonexposed in the aggregate study base manifesting the differential ef but with an expressly selected subdomain of the latter. The reference population must not fect (attributable to the exposure). In only represent a comparable nonexposed occu such a base both the exposed and the pation, but the population Itself must be simi- reference ("placebo") occupation must be represented of course. Moreover the com pared populations actually representing Id the index population in terms of extra neous and otherwise uncontrollable determi nants of the mortality under study. The selectivity in the formation of tne compared sub them should be such that the expected populations in the study base is the nonex- mortality difference between them, eonditional on whatever confounders will be perimental counterpart of randomization and other aspects of the deliberate assignment of study subjects to the compared categories ~o? controlled in the analysis, is indeed a the determinant at issue. As was noted, such reflection of the effect under study. selectivity is of particular importance in oc In occupational mortality studies it is cupational mortality studies due to the com mon lack of data on potential confounders and commonplace that only age, gender, rac~ the consequent inability to control confounding and calendar time can be controlled di in the analysis. rectly. In such instances, it is necessary to define the study base so hat it is not Comparability of mortality information confounded within the categories defined by these characteristics alone. Therefore, For the compared populations it is neces conditional on these characteristics, the sary to obtain comparable information on compared occupational populations are to the aspect of the mortality under study. In have similar mortalities (from the illness experimental studies the equivalent goal of interest) -- apart from whatever effect is commonly pursued by the use of double the exposure has! This requirement of blind procedures of outcome assessment. e comparability of the index (exposed) and In occupational mortality studies it is :s reference (nonexposed) populations may generally necessary to use routine re il be thought of in terms of forces of entry cordings of deaths and the causes of death into, and exit from, these populations. A as outcome information. The accuracy of Pfoblem can arise only insofar as entry such routines can vary according to occu e and/or exit is related to the risk of death pation and can depend on the quality of :e from the illness of interest (as indicated, health services in general, suspicion that il eg, by the presence or absence of the ill the occupation might be responsible for ness itself). More specifically, for con deaths from the cause at issue, concern founding to be a problem, an indicator of for insurance and liability, and other risk must have different implications for factors. 1]bus it is again necessary to re the compared populations with respect to sort to selection as a substitute for control, entry and/or exit. By the same token, if that is, the use of a study base in which 55 752463 0043 the compared subpopulations are inherently"s'Httliail With respect to tne accuracy of (routine) intormation about the deaths of interest. Comparability of mortality odds The presented issues of valid contrast are, as has been noted, familiar in experimental research; the three aspects of validity that are pursued through the deliberate and selective formation of occupational con trast are the counterparts of (i) arranging for a suitable "placebo" ("sham") treat i ment, (ii) randomly allocating the treat ments, and (iii) "blinding" informants/ observers in regard to the treatment category of any particular subject in the study base. While these issues of validity are of concern in all studies of occupational mor tality. an added problem of validity has ta be dealt with in situations in which the soiirce oi intormation is death certificates afone..This problem, which has no familiar counterpart in experimental studies, is not one of valid formation of the study base so that the contrast between its index (exposed) and reference (nonexposed) subdomains truly represents the effect at is sue. Instead, it has to do with the validity of information about the contrast in the study base, given that the respective sizes of the compared subdomains of the base must be assessed from death certificates. The classical way of making use of deaths from other causes is the computa tion of the proportions that the deaths of \\> interest represent among all deaths in the compared occupational populations (3, 13, 22, 26). Such mortality proportions ("pro portionate .mortalities") are proportional to tne respective mortality rates only on the demanding assumption that the total death rates are the same for the compared populations (3). This problem is avoided 1by the use of an alternative measure of y mortality, the odds of dying of the disease of interest, conditional on dying either of it or of any of the auxiliary (reference) diseases (18). Such mortality odds are proportional to the respective mortality rates on the con dition that the numbers of deaths from the reference diseases involved in the odds are proportional to the respective amounts of population-time between/among the compared population. In other words, the mortality odds is a suitable parameter of outcome for comparative purposes if the incidence rate for the reference deaths is the same for the compared populations (18). This situation again poses a need for selectivity -- in this instance as to which other deaths, in terms of disease(s), are to be employed in the auxiliary capacity in the formation of the mortality odds. The two requirements for the reference deaths to be used are: 1. The compared occupations must have identical effects on mortality from the reference diseaseTsT This condition is satisfied whenever the reference disease(s) are unrelated in their occurrence to all differential exposures between the index and reference occupations. 2. The empirical contrast must be valid with respect to confounding and the com parability of information regarding the reference disease(s) -- analogously with the requirements related to mortality from the index disease under study. Example 3. Consider again the study of lung and nasal cancer mortality in relation to nickel exposure, with those in "all other" occupa tions as the reference population. Death cer tificates were the only source of information on the study base (nickel workers plus "all other" workers), and the relative sizes of the compared populations were estimated by the use of deaths due to all other diseases. This procedure was valid insofar as two conditions were met. First, nickel refining and "all other" occupations had to have identical effects on mortality from diseases other than lung and nasal cancer. Second, selection into and out of the compared populations had to be similar with respect to such other mortality, and the detection and certification of these deaths had to be similar between the nickel refiners and the population in "all other" occupations. All of these assumptions are difficult to judge and tenuous by virtue of the use of "all other" oc cupations and all other deaths. The "healthy worker eflect" In the literature with which we are familiar, there is no rigorous definition of the "healthy worker effect." This term usually refers to a tendency for any par ticular employed population to have lower 156 mortality than the general population. dell et al (25), the term would be a mis The tendency has been observed for a leading misnomer. variety of occupations and causes of death (4, 5, 8, 9, 10, 14, 19, 23, 24). Thus an ob served-to-expected (O : E) ratio of less than Acknowledgment one might still suggest excess mortality as long as the "general population" is used as the reference population. This problem is not resolved by any ef The writing of this paper was supported by grant 5P01CA06373 from the National Cancer Institute. fort to find a universal, nonunity refer ence value for the O: E ratio [0.9, say, as References discussed by Goldsmith (11)J. The reason is. that the magnitude of the healthy worker 1. Axelson O, Dahlgren E, Jansson CD, etlect is not constant but varies according Rehnlund SO. Arsenic exposure and mor tq many factors, le, (ifrrgause of death (4. j>J. 0| 10, 14, 16, nC*23, 24), (ii) demo graphic factors fit varies by occupation tality: A case-referent study from a Swedish copper smelter. Br J ind med 35 (1978) 8--15. 2. Ciocco A, Mancuso T, Thompson DJ. Four and work category (4. 5, 8, 9, 10, 14, 16, years mortality experience of a segment of l5, 2il, 24. 27). is usually stronger for non the United States working population. Am whites than whites (4, 5, 14, 16) and stronger for the young than for the old (9, i publ health 55 (1965) 587--595. 3. Decoufle P, Thomas TL, Pickle LW. Com parison of the proportionate mortality ra lb), generally decreases with early retire tio and standardized mortality ratio risk ment [6, 28). etc.J, and (iii) time lag since starting the work or since the zero time of a cohort [It is prominent at the beginning measures. Am j epidemiol 111 (1980) 263-- 269. 4. Decoufle P, Wood DJ. Mortality patterns among workers in a gray iron foundry. and tends to decline with the nassaup nf Am j epidemiol 109 (1979) 667--675. time (6, 9, 16, 20, 24, 28).] Quantification of the healthy worker effect specific for such factors also does not seem to provide a 5. Delzell E. Monson RR. Mortality among rubber workers: III Cause-specific mor tality. 1940--1978. J occup med 23 (1981) 677--684. general solution to the problem. Rather. 6. Delzell E. Monson RR. Mortality among the ultimate solution is' to rely on proper study designs so that there is no appreci-. able healthy worker effect to begin with. rubber workers: IV General mortality pattern. J occup med 23 (1981) 850--856. 7. Doll R. Cancer of the lung and nose in nickel workers. Br j ind med 15 (1958) As many authors have pointed out, the healthy worker effect arises from the use of the general population as the reference 217--223. 8. Enterline PE. Mortality among asbestos products workers in the United States. Ann ny acad sci 132 (1965) 156--165. population (6. 8, 9, 10, 11, 14, 16, 19, 20, 9. Fox AJ, Collier PF. Low mortality rates 23, 24, 27). Each occupational setting has its characteristic requirements and in centives for job entry (2, 6. 8. 9. 10. 14. 16. in industrial cohort studies due to selec tion for work and survival in the in dustry. Br j prev soc med 30 (1976) 225-- 230. J. 1^, 20, 24) and exit (2, 6, 9, 10, 14, 16. 20), 10. Gilbert ES, Marks S. An analysis of the yj and these, when different for the index mortality of workers in a nuclear facility, occupation and the "genera) population'' 1979. Radiat res 79 (1979) 122--148. 11. Goldsmith JR. What do we expect from ana also when related to mortality, pro an occupational cohort? J occup med 17 duce the healthy worker effect. Bv the (1975) 126--127. same token, if the use of the general population is replaced by the use of an oc cupational population with comparable 12. Hill AB. Observation and experiment. New engl j med 248 (1953) 995--1001. 13. Kupper LL. McMichael AJ, Symons MJ, Most BM. On the utility of proportional job entry and exit factors, then there is mortality analysis. J chronic dis 31 (1978) no healthy worker effect. The healthy worker effect is a reflection of the incomparability of compared populations only* 15--22. 14. Lloyd JW. Ciocco A. Long-term mortality study of steelworkers: I Methodology. J occup med II (1969) 299--310. -- a matter of confounding -- and it is 15. Mazumdar S. Redmond C, Sollecito W, not a result of the incomparabilitv of the effects or information For the latter types of incomparability, as discussed by Shin- Sussman N. An epidemiological study of exposure to coal tar pitch volatiles among coke oven workers. J air pollut control assoc 25 (1975) 382--389. 157 752463 0045 McMichael AJ. Standardized mortality ra tios and the healthy worker effect: Scratching beneath the surface. J occup med 18 <19761 165--168. Miettinen OS. Design options in epidemio logic research: An update. Scand j work environ health 8 (1982): suppl 1, 7--14. 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Occupational health prac tice. Butterworth, London 1981, pp 266-- 270. 27. Vinni K, Hakama M. Defining expected mortality in occupational studies: Scand j work environ health 5 (1979) 297--303. 28. Vinni K, Hakama M. Healthy worker ef fect in the total Finnish population. Br j ind med 180--184. Received for publication: 23 June 1982