design and conduct of occupational epidemiology studies: i. design aspects of cohort studies

American Journal of Industrial Medicine 15:363-373 (1989)

Design and Conduct of Occupational Epidemiology Studies: 1. Design Aspects of Cohort Studies

Harvey Checkoway, PhD, Neil Pearce, PhD, and John M. Dement, PhD

Cohort and case-control studies are two standard approaches for investigating the etiology of occupational diseases. This paper, which is the first of a four-part series, contains a review of the design features of occupational cohort studies. Topics discussed include the basic features of prospective and historical cohort studies, options for defining the cohort, disease incidence ascertainment, and considerations involved in planning an occupational cohort study. Subsequent papers in this series will focus on data analysis of occupational cohort studies and the design and analysis of occupational case-control studies.

Key words: cohort studies design, epidemiologic methods, occupational health follow-up

INTRODUCTION

In-depth study of associations of hazards to health and occupational exposures requires enumeration of a cohort of workers and measurement of the cohort’s disease rate experience in relation to workplace exposure levels. Cohort and case-control designs are two common approaches that are especially useful for the study of chronic diseases, which represent delayed effects of prolonged exposures. This paper, which is the first of a four-part series, provides a review of the design of occupational cohort studies. In this first paper emphasis will be placed on options for defining the cohort and methods for determining disease incidence. The second paper in this series [Checkoway et al., 19891 concerns the analysis of cohort study data, and the last two papers are devoted to the design and conduct of occupational case-control studies. Some of the methodological points made in these papers will be illustrated with an example of a cohort mortality study of asbestos textile plant workers [Dement et al., 1983a,b].

This series of papers is intended to provide practitioners of occupational

Department of Environmental Health, School of Public Health and Community Medicine, University of washington, Seattle (H .C. ). Department of Community Health, Wellington School of Medicine, Wellington Hospital, Wellington, New Zealand (N.P.). National Institute of Environmental Hcalth Scicnces, Office of Occupational Health and Technical Services, Research Triangle Park, NC (J.M.D.). Address reprint requests to Harvey Checkoway, Department of Environmental Health, SC-34, University of Washington, School of Public Health and Community Medicine, Seattle, WA 98195. Accepted for publication October 28, 1988.

0 1989 Alan R. Liss, Inc.

364 Checkoway et al.

DISEASE r EXPOSED a q

SOURCE POPULATION

L NO DISEASE

REMOVE EXISTING (PREVALENT) CASES OF DISEASE

L NO DISEASE

.P - . I

END OF TIME FOLLOW-UP BEGINS FOLLOW-UP

Fig. 1. Flow diagram of the cohort study design

epidemiology and professionals in related disciplines with an overview of fundamen- tal techniques. Presentations of more advanced topics, such as mathematical modeling of exposure-response relationships, can be found in specialized texts and journal publications devoted to these issues. Some useful citations relevant to advanced design and analysis methods will be offered in the present series of articles.

BASIC COHORT STUDY DESIGN

Cohort studies can be classified as either prospective or historical, depending on whether follow-up occurs during future or historical time. Some cohort studies combine features of both, in that follow-up begins at some point in the past and continues prospectively into the future. Irrespective of the timing of the study, all cohort studies share the same basic design features: 1) enumeration of the study population exposed to the factor(s) of interest; 2) identification of a comparison (reference) population; 3 ) follow-up of the cohort and determination of disease incidence; and 4) comparison of disease rates between the cohort and the comparison population. The comparison population may be external to the study cohort, such as the national population, or may consist of a subset of cohort members with the lowest exposures, i.e., internal reference group. Figure 1 depicts the basic design of a cohort study. In a prospective cohort study, would be the present and t l would be some point in the future. In an historical cohort study, to would be a time point in the past and t l would represent the present or some time close to the present.

Historical cohort studies are far more common than prospective studies in occupational epidemiology; therefore, most of the discussion will focus on the former. However, because the basic methodological features of all cohort studies are the same, the discussion will also pertain to other types of cohort studies.

DEFINING THE STUDY COHORT Selecting the Study Population

An occupational cohort can be defined in several ways. The simplest situation is selection of all workers ever employed in one factory or manufacturing complex. A second option is to include cohort workers from multiple plants operated by

Design Aspects of Cohort Studies 365

I I

I *WORKER A

I *WORKER B

I I I

I I I

I I I I I

I *WORKER C

+WORKER D

WORKEGE A t

To +; TIME Ti PLANT COHORT END OF FIRST ENUMERATED FOLLOW-UP OPERATES AS OF THIS

DATE

Fig. 2. Cohort membership inclusion options.

different companies but engaged in similar industrial processes. The second option is desirable when the numbers of workers from individual plants are small. In fact, one may include workers from similar facilities located in different countries, as was done in a recent study of workers exposed to man-made mineral fibers [Saracci, 19861. A third type of cohort consists of members of a trade union or professional organization that includes workers from numerous worksites in diverse industries, but who share a common set of occupational exposures. Examples of the last type are cohort studies of North American insulation workers [Selikoff et al., 19791, meatworks union members [Johnson et al., 19861, and radiologists and other medical specialists [Matanoski et al., 19751. A fourth and special type of cohort consists of registered cases with occupational diseases. Here the interest would be studying mortality from the registered disease as well as the incidence and mortality of other diseases. An example is a mortality study among pneumoconiosis cases registered in the Swedish Pneumoconiosis Registry [Westerholm, 19801. Such cohorts typically represent the highest risk segments of the source occupational populations.

The advantage of restricting the cohort to workers from one facility is that characterization of exposures may be more consistent and precise when environmental and employment data are obtained from a single source than would be the case when data of varying levels of completeness and quality are combined from multiple facilities [Marsh, 19871. The potential gain in uniformity and accuracy of data needs to be evaluated in light of potential gains in study size that could be achieved from pooling data from multiple facilities.

Figure 2 illustrates cohort definitions for an historical cohort study with depic- tions of five hypothetical workers. In the ideal case, one would enumerate all workers employed since the beginning of plant operations, to, and thus Workers A, B, C, D, and E would all be included in the cohort. By analogy, in a study of members of a trade union, to would be the date when the first members enrolled in the union (although this date would not necessarily coincide with the earliest beginning date of the companies or trades represented by union membership). Often, practical difficulties arise when records for workers that date back to to are not available. As a compromise, one could choose some date, tfO, for which a sufficiently large cohort can be constructed from personnel and other records. In the example of Figure 2, only Worker E would not be eligible for inclusion in the cohort.

366 Cheekoway et al.

When the date of cohort inception, which ultimately corresponds to the earliest beginning date of follow-up, is later than the date of a plant’s first operation (i.e., t’,, > to), the cohort may include workers hired at various times prior to to, and thus employed for different lengths of time prior to t ’o. The cohort may be heterogeneous with regard to prior exposure, and hence disease risks, especially when exposure intensities have varied over time [Weiss, 19831. In this situation, stratification of cohort members with respect to length of employment and year of initial hire can mitigate potential biases resulting from inappropriate pooling of cohort members with dissimilar employment histories. Stratification of the cohort’s person-time experience will be discussed in some detail in the second paper of this series [Checkoway et al., 19891.

Fixed and Dynamic Cohorts A further consideration in defining a study cohort is whether the cohort is

restricted to workers employed as of some date, either to or tfo, or whether the cohort will include these and workers hired subsequent to that date, i.e., whether the cohort is $xed or dynamic. In the context of Figure 2, and assuming that employment data are only available for workers hired on or later than t ’ o , a fixed cohort would include Workers A, B, and C, but not D, who was hired after t’o. Worker D would be included in a dynamic cohort, however.

The choice of a fixed rather than dynamic cohort may be dictated by data- availability constraints. For example, data may only be available for workers employed as of some particular date. Alternatively, studying a fixed cohort of workers who experienced an unusual exposure, such as an industrial accident, during a particular time period (usually brief) might be more efficient than studying a dynamic cohort of workers, many of whom would not have had the same exposure. Zack and Suskind’s [1983] study of a fixed cohort of workers potentially exposed to high intensities of dioxins during an accident at a trichlorophenol manufacturing plant is a case in point.

In most instances it is preferable to enumerate dynamic cohorts. There are two reasons for this recommendation. First, human populations are naturally dynamic; births and deaths, which are analogous to hirings and terminations in occupational cohort studies, occur continuously. Thus, a dynamic, rather than fixed, cohort more closely mimics the source population. Second, dynamic cohorts usually will include more subjects than will fixed cohorts. Consequently, the effect of exposure on disease occurrence can be measured with greater precision. Given adequate information about special exposure circumstances, the investigator can isolate for detailed examination fixed cohorts that are segments, or subcohorts, of a dynamic cohort.

Cohort Restriction When enumerating a cohort, the investigator should attempt initially to identify

as many workers as possible without invoking any restrictions. Arbitrary exclusions from enumeration of workers considered unlikely to be exposed, e.g., plant managers or office workers, will be wasteful of information insofar as removal of the lowest exposed persons will diminish the precision of observed exposure-response relationships. Decisions regarding exposure status should be deferred until a thorough evaluation of employment history has been made. In some instances inspection of complete employment data will reveal that office workers and other “salaried”


personnel held exposed jobs in the industry before assuming their more recent positions, in which case their inclusion would be particularly justified.

Some investigators prefer to restrict dynamic cohorts to workers first employed during a particular time interval (e.g., up until 10 years before the end of follow-up), thus allowing for a minimum follow-up duration for all cohort members. This approach is usually adopted to allow for minimum induction and latency times for delayed exposure effects. Restrictions of this type are not necessary at the stage of cohort enumeration if latency analyses are to be performed on the data, but they may be justifiable as a means of reducing the size of the study, and hence its cost.

There are, of course, exceptions to the general guideline of enumerating all workers for whom data can be assembled. Limited resources may dictate that the study be restricted to workers assumed to be at highest risk. This might involve restriction of the cohort to workers employed in the most intensely exposed jobs or for the longest durations in the industry. However, restriction of this type should not be made routinely to maximize efficiency because this approach reduces the ability to examine exposure-response gradients. A second reason to censor cohort enumeration is to eliminate workers who were not engaged in the tasks characteristic of the facility or occupational group under study. For example, in a study of a manufacturing plant work force, it would be justifiable to exclude from the cohort the plant construction workers under contract from another company. In this case, restriction would help focus the study on health effects related to the relevant exposures.

Restrictions on gender or race are made ordinarily for convenience. In the United States most occupational cohorts traditionally have consisted of white males, partly because this group comprises the majority of many work forces, but also because vital status tracing for white males is more easily accomplished than for women or nonwhites. There is no scientific basis for limiting the study population to any particular gender or race group. Indeed, studying all workers for whom health and exposure data can be obtained enlarges the study size and permits inspection for particular subgroups more or less susceptible to adverse exposure effects, e.g. , women in early stages of pregnancy.

A minimum length of employment criterion for cohort inclusion is imposed in many studies as a means of studying the workers at highest risk. The choice of a minimum employment duration is arbitrary unless dictated by constraints on data availability or resources. Limiting the cohort to long-term workers, such as the so-called vested employees or retirees, can simplify the study insofar as enumeration and follow-up are ordinarily easiest for this group [Collins and Redmond, 1976; McMichael et al., 19761. However, confining the study to retirees or vested workers will give an incomplete (and possibly biased) picture of disease risks for the cohort because deaths that occurred before retirement would not be observed. Also, the ability to detect exposure-response relationships may be diminished because the study cohort would be heavily weighted by workers with the longest employment durations.

Restrictions based on exposure potential and presumed toxicity thresholds can be misleading. For example, if there is an agent in the industrial environment that poses demonstrable health risks following even brief periods of exposure, then there would be no justification for imposing a minimum employment duration criterion. There are situations in some industries where the most intense exposures occur very early during employment, such as during apprenticeship or on initial assignment.


Occupational accidents, for example, typically occur among the least experienced workers [Baker, 19751.

Two other related considerations are variability in the quality of exposure data and nonoccupational disease risk factors, both of which may be related to employment duration. Workers employed for very short durations, e.g., several months or less, in some industries are assigned to jobs designated by the nonspecific “laborer” descriptor. Laborer jobs, like maintenance jobs, can be more difficult to characterize according to exposure type or intensity than jobs or tasks held by long-term workers. Furthermore, short-term workers, especially transients, may have atypical (disadvan- tageous) lifestyles, and thus different baseline disease risks than other workers. This may explain why some analyses comparing disease rates between workers, classified according to length of employment in industries with known hazardous exposures [Peto et al., 1985; Simonato et al., 19861, show disease excesses among the short-term workers (e.g., employed for less than 1 year). Thus, relative mortality excesses among short-term workers may reflect the absence of a healthy-worker effect in this group [Fox and Collier, 1976; Gilbert, 19821.

There is no simple rule for selecting a minimum employment duration criterion. Decisions need to be made in light of the balance between potential gains in information and study precision achievable by including short-term workers on the one hand, and possible introduction of selection and misclassification biases and added costs on the other.

Restriction with respect to a minimum duration of time since first exposure is often made to allow for disease latency. Here again, the choice of a minimum duration is arbitrary. Latency intervals vary by disease and etiologic agent; consequently, it is generally inadvisable to impose too stringent of a minimum time since exposure onset criterion (e.g., 20 years) on cohort inclusion in studies of multiple endpoints. However, when resources are limited, a minimum duration inclusion criterion may be warranted if most or all of the primary diseases of interest ordinarily exhibit long latency periods, e.g., most cancers. When possible, one should avoid restrictions of this type because disease latency can be addressed in the analysis by stratification with respect to follow-up duration, or by applying exposure-weighting schemes that eliminate from consideration potentially irrelevant exposures [Rothman, 1981; Axelson, 19851. The pattern of disease risk in relation to time since exposure onset is an important study finding; thus, studies including workers with varying times since exposure onset would be preferred to those of restricted cohorts.

DETERMINATION OF DISEASE FREQUENCY Mortality and Morbidity Studies

Ideally, one would obtain data on the incidence of both fatal and nonfatal diseases. In practice, however, many occupational cohort studies are limited to mortality because such data are more routinely retrievable. Morbidity, or incidence, studies are accommodated best when the cohort can be linked to population disease registers, such as cancer registries, or when special incidence surveys are conducted among the work force. The relative advantages of mortality and morbidity data are well recognized. Therefore the only point to emphasize is that care should be taken to ensure comparability of data sources in studies involving morbidity comparisons between an occupational cohort and an external comparison population. More vigilant


case-finding among the cohort than in the comparison population at large can produce a spuriously elevated risk estimate. This concern is most relevant for diseases that may be underreported by population-based registries. A recent report of a malignant melanoma excess at a nuclear research laboratory [Austin et al., 19811 has been criticized on these grounds.

Follow-up Procedures In mortality studies, tracing of vital status is accomplished by linking cohort

members’ personal identifiers (name, date of birth, registration number, etc.) with data compiled on a national basis. In the United States, the Social Security Admin- istration and the National Death Index are the principal sources of vital status information [Kelsey et al., 19861, whereas in Great Britain the Central Record Office of the Ministry of Pensions and National Insurance [OPCS, 19781 serves this purpose. Centralized population registers maintained in several countries, including Denmark, Sweden, and Finland, greatly facilitate epidemiologic research [Riihimakii et al., 1982; Lynge, 1985; Gustavsson et al., 19861. Ancillary sources of vital status data include motor vehicle registration bureaus, voter registration listings, postal offices, and town and city directories.

Vital status tracing is more difficult in countries that lack national population registers or maintain only regional registers. For example, in their study of workers from a German rock-wool factory, Claude and Frentzel-Beyme [ 19841 determined vital status from multiple enquiries made to worker registration offices and from contacts made at workers’ last known addresses or places of birth.

A vital status ascertainment rate of 95 percent or higher is a desirable target, although rates of 90 to 95 percent may be acceptable in large cohort studies. If, for example, tracing is especially poor for workers who left employment before retirement, and if many of these workers terminated because of occupational diseases, then a low tracing rate (e.g., less than 90 percent) would result in underestimated disease risks. The practical solution would be to conduct separate analyses for subgroups of the cohort defined by age at termination of employment.

Some workers will remain untraced either in a mortality or morbidity study. There are several options for handling losses to follow-up and their person-time contributions to the study [Monson, 19801. These include: 1) deleting lost to follow-up workers from the study; 2) assuming that all untraced workers remained free of disease at the end of the study, and thus contribute person-years to that time; and 3 ) counting person-years only until the date of last contact, typically the date of termination from the industry. The third option is most defensible, as all known information (person-time) is included in the analysis but requires few unverifiable assumptions regarding other time periods. The first option, deleting untraced workers, is unnecessarily wasteful of information, whereas the second will result in underestimated disease risks among the cohort [Vena et al., 19871.

SELECTION OF A COMPARISON POPULATION

It has become a common practice to choose the national population for comparison in the overall analysis of disease rates. There are several advantages of using a national (external) comparison. First, it is generally of some interest to know how rates in the cohort compare with national rates, even if the cohort and the


comparison population may have different distributions of confounders. Disease rates, stratified by gender, race, year, and age at death, are frequently published on a national basis and are convenient sources for comparison. Also, national rates are numerically stable for most diseases, thus improving the precision of the comparisons. At times, it may be desirable to use a regional external comparison population, such as the state or province, as a means of controlling geographic differences in disease incidence or diagnostic customs. Difficulties arise when rates for the region are not published in a form suitable for stratified analysis by covariates, or when the regional rates are based on small numbers.

The primary shortcoming of selecting a national or regional comparison population is that mortality comparisons may be biased by the often noted healthy-worker effect, which is characterized by depressed all-causes mortality among the cohort. This phenomenon has been discussed by numerous authors [Enterline, 1975; Delzell and Monson, 1981; Wen and Tsai, 1982; Monson, 19861. The healthy-worker effect can be viewed as an example of selection bias, wherein the selection of the national population as a reference is inappropriate because it contains the chronically ill and hospitalized and persons otherwise unfit to seek and maintain employment. Alterna- tively, the healthy-worker effect can be considered as the result of confounding by unmeasured predictors of health [Monson, 19861.

Lowered mortality rates from cardiovascular diseases and nonmalignant respiratory and digestive system diseases are the main contributors to the overall mortality deficit [Enterline, 1975; McMichael, 19761. The healthy-worker effect is not seen universally, however. An apparent absence of a healthy-worker effect may arise when there is an important health hazard in the industry, or it may result from a cohort that is predominatkd by short-term workers with potentially deleterious lifestyles [Gilbert, 19821.

There are several ways to minimize bias attributable to the healthy-worker effect. One strategy is to identify employed and retired workers from the population at large as an external reference population. Linking national census data containing employment information with mortality data can be used for this purpose [Fox and Adelstein, 19781. Unfortunately, such linkage cannot be accomplished in most countries.

Alternatively, the comparison population may be selected from among workers in another industry without the exposures of interest. For example, Hernberg et al. [ 19701 used the latter approach in their study of cardiovascular disease among viscose rayon factory workers; the comparison group consisted of paper-mill workers not exposed to the suspected etiologic agents, carbon disulfide and hydrogen sulfide.

Comparing disease rates between two industrial populations has the potential advantages of minimizing bias from the healthy-worker effect and achieving control of confounding by other factors, such as social class. However, relative excesses or deficits among the study cohort will be difficult to interpret if the reference worker cohort is exposed to the same or different disease-causing agents. To illustrate, consider a cohort study of lung cancer incidence among uranium miners in which asbestos textile manufacturing workers are chosen as the comparison group. In this instance, an excess lung cancer rate among the uranium miners would be understated or would go undetected.

A third strategy is to restrict comparisons to the person-time experience of the cohort, treating disease rates associated with the person-time in the nonexposed or


lowest exposed jobs as an internal reference category. This may not eliminate bias from the healthy-worker effect [Pearce et a]., 19861 but will usually reduce it. When an internal reference category is selected, bias may be reduced further by adjustment for time-related factors associated with the healthy-worker effect, e. g., duration of follow-up [Pearce et al., 19861. Here again, elimination of bias is not guaranteed. For example, a reduced ability to detect an exposure-response gradient may be the result of failure to take into account the influence of a factor that combines with occupational exposures in such a way as to cause the most heavily exposed workers to end employment prematurely, e.g., respiratory tract irritation from the combined effects of volatile chemicals and cigarette smoke [Robins, 19861. However, the likelihood of such biases occurring is unknown in most occupational studies. Thus, adjustment for factors such as duration of follow-up would still be warranted, even if it will not mitigate bias completely.

There are several advantages of using an internal reference population. The first is that similarity of data quality is anticipated for all groups compared. In contrast, there are usually disparities in the amounts and quality of such data between the study cohort and an external reference population. Also, similar selective forces should be at play for both exposed and nonexposed workers, thus diminishing bias from the healthy-worker effect. Two disadvantages are that unstable rates in the reference category may limit precision of effect estimates, and it may not be possible to identify a “nonexposed” internal reference group.

Ideally, one would perform analyses using both external and internal reference populations, where the former are used to identify overall patterns of disease excesses and deficits, and analyses involving an internal reference group are conducted to assess exposure-response trends. These approaches are not mutually exclusive, as, for example, one may perform exposure-response analyses using an external reference population.

PLANNING A COHORT STUDY

In principle, decisions as to which occupational cohorts warrant epidemiologic study should be made primarily on the bases of public health and scientific concerns. The occupational groups that are exposed either to known or suspected toxic substances are the obvious targets for study. However, such decisions are seldom straightforward, because one needs to anticipate the likely study results and their interpretations before embarking on cohort enumeration and follow-up. It is also important to have some prior assurance that the quality of data will be adequate for the research objective. For example, another study of lung cancer mortality among asbestos-exposed workers would do little to advance knowledge if exposure data were inadequate to specify the types of asbestos fibers and their quantities. When possible, prior surveys of plant personnel, job history, and exposure data can assist in the selection of study populations [Steenland et al., 19871.

The issue of study size requirements is often raised in the context of statistical significance testing. It is perhaps more reasonable to view study size as a predictor of the potential precision of the study results [Rothman, 19861. Estimated study size requirements for cohort studies have been discussed by several authors [Schlessel- man, 1974; Walter, 1977; Beaumont and Breslow, 1981; Armstrong, 19871, so formulae will not be presented here. Duration of follow-up and time since first


exposure are related to study size and may be important considerations for studies with long latency periods. For example, a study of 10,000 workers each followed for 1 year would be less informative than a study of 1,000 workers each followed for 10 years, despite equivalent numbers of person-years, when diseases of interest have minimum latencies of 5 years.

ACKNOWLEDGMENTS

This work was conducted during the tenure of Dr. Pearce of an Overseas Research Fellowship of the Medical Research Council of New Zealand. The authors are grateful to Dr. Sander Greenland for reviewing drafts of these papers, to Mr. David Brown of NIOSH for providing access to data, and to Ms. Melinda Fujiwara for manuscript preparation.

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design and conduct of occupational epidemiology studies: i. design aspects of cohort studies

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