principles ofstudydesign in environmental epidemiology · problemsinenvironmental epidemiology...

Principles of Study Design in EnvironmentalEpidemiologyHal Morgenstern" and Duncan Thomas2'Department of Epidemiology, University of California at Los Angeles, School of Public Health, Los Angeles, CA90024-1772; 2Department of Preventive Medicine, University of Southern California, School of Medicine, LosAngeles, CA 90033-9987

This paper discusses the principles of study design and related methodologic issues in environmental epidemiology. Emphasis is given to studiesaimed at evaluating causal hypotheses regarding exposures to suspected health hazards. Following background sections on the quantitative objec-tives and methods of population-based research, we present the major types of observational designs used in environmental epidemiology: first, thethree basic designs involving the individual as the unit of analysis (i.e., cohort, cross-sectional, and case-control studies) and a brief discussion ofgenetic studies for assessing gene-environment interactions; second, various ecologic designs involving the group or region as the unit of analysis.Ecologic designs are given special emphasis in this paper because of our lack of resources or inability to accurately measure environmental expo-sures in large numbers of individuals. The paper concludes with a section highlighting current design issues in environmental epidemiology and sev-eral recommendations for future work. - Environ Health Perspect 101 (Suppl 4):23-38 (1993).

Key Words: Study design, epidemiologic methods, environmental healts, ecologic studies, aggregate studies, causal inference

Introduction

The purpose ofthis artide is to discus the princi-ples of study design and related methodologicissues in environmental epidemiology. The focusis on studies aimed at evaluating csal hypothe-ses ding eosu to spected health haz-

ards. Because the intended audience for thisdocument indudes scientists without formaltraining in epidemiology, parts of this articlehighlight basic principles of epidemiologicreerc Nevertheless, we also try to summarze

comprehensively the current state of the art andmake recommendations for future developmentsin study design. For more tensive trment ofgeneral research principles and methods in epi-demiology, the interested reader should consult

available textbooks in this area (1-6). Moredetailed exmples of applications in environmen-

tl epidemiology may be found in severl otherbooks, such as those edited by Leaverton (7),Chiazze et al. (8), Goldsmith (9), and Kopflerand Craun (10).

Population ParametersThe major quantitative objectives of most epi-

demiologic studies are to estimate two types ofpopulation parameters: the frequency of dis-

ease occurrence in particular populations and

This manuscript was prepared as part of the Envir-onmental Epidemiology Planning Project of the HeafthEffects Insttue, September 1990 - September 1992.

*Author to whom correspondence should beaddressed.

This work was funded by the Health EffectsInstitute in Cambridge, MA. The authors would like tothank Dr. John Tukey, Dr. Sander Greenland, and othermembers of the HEI Methodology Working Group fortheir helpful comments.

the effect of a given exposure on diseaseoccurrence in a particular population.

Measures of disease frequency involvethe occurrence of new cases or deaths (inci-dence/mortality) or the presence of existingcases (prevalence). In both applications,the number of cases is expressed relative tothe size of the population from which thecases are identified. With incidence mea-sures, this denominator is the (base) popu-lation at risk (i.e., individuals who areeligible to become cases). Thus, the basepopulation of a study (or study base) is thegroup of all individuals who, if they devel-oped the disease, would become cases inthe study (3,11,12).

Disease incidence, which is central to theprocess of causal inference, can be expressedas a cumulative measure (risk) or as a per-son-time measure (rate). The cumulativeincidence (incidence proportion) or averagerisk in a base population is the probability ofsomeone in that population developing thedisease during a specified period, condi-tional on not dying first from another dis-ease (13). The term cumulative incidenceor cumulative incidence rate also is definedsomewhat differently as the integral over thefollow-up period of the hazard (rate) func-tion (14). The incidence rate or instanta-neous risk (hazard) is the limit of the averagerisk for a given period, per unit of time, asthe duration of the period approaches zero.The average rate (incidence density) for agiven period is estimated as the number ofincident events divided by the amount ofperson-time experienced by the base popula-

tion. For example, a rate of 0.001/yearmeans that we would expect one new case tooccur for every 1000 person-years of follow-up (e.g., 100 disease-free people followed foran average of 10 years).

Although there are many quantitativemethods for expressing the magnitude of astatistical association between two variables(e.g., exposure status and disease occur-rence), we are usually interested in a specialclass of such measures that reflect the neteffect of the exposure on disease occurrence(i.e., causal parameters). In general, acausal parameter for a target population is ahypothetical contrast-in the form of a dif-ference or ratio-between what the fre-quency of disease would be if everyonewere exposed (at a given level) to what thefrequency would be if everyone were unex-posed (often called the reference level)(15). When this difference for a specificexposure is not zero (the ratio is not one),we say that the exposure is a risk factor forthat disease in the target population. Inpractice, we estimate causal parameters indi-rectly by comparing disease frequency for anexposed group with disease frequency for anunexposed group. Epidemiologists typicallyestimate the risk or rate ratio (often calledthe relative risk) by comparing the exposedpopulation with an unexposed population.The key assumption of this statisticalapproach is that the risk or rate observedfor the unexposed group is the same (withinconfounder strata) as the risk or rate thatwould have been observed in the exposedgroup if that group had not been exposed

Environmental Health Perspectives SupplementsVolume 101, Supplement 4, December 1993

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(16). Thus, the (true) risk ratio may beinterpreted as a causal parameter, which is thenumber of cases actually occurring in theexposed (target) population divided by thenumber of cases that would have occurred inthe absence of exposure.

Certain measures of association, such ascorrelation coefficients and standardizedregression coefficients, do not, in general,reflect any causal parameters. The reason isthat the magnitude of these measures dependsin part on the relative variances of the expo-sure and disease variables, which are influ-enced by the sampling strategy (i.e., noncausalparameters) (17,18). Another measure ofassociation, the odds ratio, is used in certaintypes of epidemiologic studies (case-controldesigns) to estimate the risk or rate ratio indi-rectly when we cannot first estimate the inci-dence rate or risk in the exposed and unexposedpopulations (1-619,20).

Problems in EnvironmentalEpidemiologyThere are several general problems in envi-ronmental epidemiology that tend to limitcausal inference and, therefore, shapedesign decisions.

Long Latent Periods. The intervalbetween first exposure to an environmentalrisk factor (or the start of causal action of thisfactor) and disease detection (or symptomonset) may be many years or even decades.Such long latent periods are pardy due to lim-itations ofmedical technology and incompletesurveillance for detecting disease; yet they arealso due to a prolonged induction period inwhich years are needed for the disease processto begin (5). The term latent period also isused more specifically to indicate the hypo-thetical interval between disease initiation anddetection (5). Refer also to Armenian andLilienfeld (21) who discuss altemative defini-tions of latency. Unfortunately, long latentperiods produce important practical con-straints on our ability to estimate exposureeffects. The investigator must either observesubjects for many years or rely on retrospec-tive (historical) measurement of key variables.The latter altemative may be infeasible for cer-tain types of exposures or in certain popula-tions. Even when feasible, however,retrospective measurement usually increasesthe amount of error with which exposures aremeasured (see below). Furthermore, the levelof most environmental exposures and manyextraneous risk factors changes appreciably orunpredictably over time; long latent periods,therefore, seriously complicate our ability toestimate effects (22).

Errors ofExposure Measurement. Amajor challenge in environmental epidemi-

ology is to measure accurately each individ-ual's exposure to hypothesized risk factors(i.e., the biologically relevant dose [ Thomasand Hatch, this issue]). This task is madevery difficult by the lack of informationabout environmental sources of emission,the complex pattern of most long-termexposures, the individual's ignorance of pre-vious opportunities for exposure, the lack ofgood biological indicators of exposure level,and the lack of sufficient resources to collectindividual exposure data on large popula-tions. The consequences of exposure mis-measurement are probable bias in theestimation of effect (see "Sources ofEpidemiologic Bias") and possible loss of pre-cision and power with which effects are esti-mated and tested (23,24). The problem andissues of exposure measurement are discussedmore thoroughly by Hatch and Thomas inthis issue.

Rare Diseases, Low-Level Exposures,and Small Effects. In most epidemiologicstudies of environmental hazards, statisticalobjectives may be further compromised bythe infrequent occurrence of the disease oroutcome of interest, by the low prevalenceor levels of environmental exposures in thegeneral population, and by the search forsmall effects (for which the true rate ratio isbetween 0.5 and 2). A critical consequenceof these features is usually substantial lossof precision and power with which effectsare estimated and tested. In addition, itbecomes more difficult for the investigatorto separate the effect of the exposure ofinterest from the distorting effects of extra-neous factors. Causal inference can thenbe seriously compromised.

Research Objectives andStrategiesGiven the above problems, epidemiologistsmust carefilly plan their studies, analyze theirdata, and interpret their findings. Inaccurateresults reflect both random errors of estima-tion (chance) and systematic errors or bias.An epidemiologically unbiased or valid esti-mate of a causal parameter is one that isexpected to represent perfectly (aside fromchance) the true value of the parameter in thebase population.

Source ofEpidemiologic BiasA common framework for describing thevalidity of epidemiologic research is to con-sider three sources of bias in the estimationof effect: selection bias, information bias,and confounding (2). Despite the practi-cal attractiveness of this framework, thethree types of bias are not entirely separateconcepts. The amount of confounding, for

example, can depend on how subjects areselected.

Selection Bias. Selection bias meansthat the way in which subjects are selectedinto the study population or into the analy-sis (due to lost subjects or missing data)distorts the effect estimate. In general, thisproblem occurs when either disease statusor exposure status influences the selectionof subjects to a different extent in thegroups being compared. Selection bias ismost likely to be problematic when the investi-gator does not identify the base populationfrom which study cases arose.

Information Bias. Information biasmeans that the nature or quality of measure-ment or data collection distorts the effectestimate. The primary source of informa-tion bias is error in measuring one or morevariables. When exposure status or diseasestatus is misclassified, bias usually occurs. Ifthe probabilities of misclassification of eachvariable are the same for each category of theother variable (nondifferential misclassifica-tion) and if the errors for different variablesare independent, the estimate of effect isusually biased toward the null value (indi-cating no effect). Possible exceptions to thisprinciple of nondifferential misclassificationleading to conservative effect estimates arisewhen the misclassified exposure variable iscategorized into more than two groups(25). In other situations involving differ-ential misclassification (unequal misclassifi-cation probabilities) or correlatedmeasurement errors, the effect estimatemay be biased in either direction. In manystudies, therefore, the magnitude of mis-classification bias is difficult to predict,especially when other biases are operating.

Confounding. Confounding refers to alack of comparability between exposuregroups (e.g., exposed versus unexposed)such that disease risk would be differenteven if the exposure were absent or thesame in both populations (16). Thus,confounding is epidemiologic bias in theestimation of a causal parameter (see"Population Parameters"). Because there isno empirical method for directly observingthe presence or magnitude of confounding,in practice we attempt to identify and con-trol for manifestations of confounding.This is done by searching for differencesbetween exposure groups in the distribu-tion of extraneous risk factors for the dis-ease, which are called confounders. Thus,a confounder is a risk factor (or proxy) thatis associated with exposure status in thebase population. A covariate meeting thesecriteria is not a confounder, however, if itsassociation with the exposure is due entirely to


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the effect of the exposure on the covariate;for example, the covariate might be anintermediate variable in the causal pathwaybetween the exposure and disease. If theexposure and covariate are time-dependentvariables, it is possible for that covariate tobe both a confounder and an intermediatevariable (see "Cohort Study").

The Need for Covariate DataIn addition to the exposure of interest,there is the need in virtually all epidemio-logic studies to collect data on other knownor possible risk factors for the disease.These covariates may be relevant to theexposure effect in three ways: a) as con-founders, b) as intermediate variables, andc) as effect modifiers.

The effects of confounders must becontrolled or removed analytically toobtain unbiased estimates of causal para-meters. This control is usually achievedthrough stratification or model fitting.The assessment and control of intermediatevariables can elucidate causal mechanismsthat explain exposure effects (26). Thisapproach often leads to new etiologichypotheses and new intervention strategiesfor disease prevention.

When the exposure-effect measurevaries across categories or levels of anotherfactor, we call the second factor an effectmodifier; this statistical phenomenon iscalled effect modification or an interactioneffect. The assessment of effect modifica-tion is model-dependent, meaning that itdepends on what (causal) parameter is usedto measure the effect (2-6). For example,an extraneous risk factor that does notmodify the risk ratio for the exposure willmodify the risk difference. The assessmentof effect modification is important forproperly specifying the predictors in statis-tical models (2,14), for making inferencesabout possible biological (causal) interac-tions between exposures (e.g., synergy) (5),and for generalizing one's results to otherpopulations (see "Cohort Study").

Types ofRmechThere are three general design strategies for con-ductng population research: a) experiments inwhich the investigators randomly assign (ran-domize) subjects to two or more treatment(exposure) groups; b) quasi-experiments inwhich the investigators make the assignmentsto treatment groups nonrandomly; and c)observational studies in which the investiga-tors simply observe exposure (treatment) sta-tus in subjects without assignment (2).Although some epidemiologists dassify thefirst two types as intervention studies, obser-

vational studies might also involve the evaluationof an intervention that was not implemented orcontrolled by the investgators. Social scientistsoften use the term quasi-experiment to meanany type ofnonrandomized study (27).

Experiments. In a simple experiment,there are usually two treatment groups.One group is assigned to receive the newexperimental intervention and the other(control) group is assigned to receive nointervention, a sham intervention (placebo),or another available intervention. Simplerandomization of individuals to treatmentgroups implies that all possible allocationschemes of assigned subjects are equallylikely (28). Following randomization, theinvestigator follows subjects for subsequentdisease occurrence or change in outcome sta-tus. A comparison of risks between treatmentgroups provides an estimate of a causalparameter reflecting the treatment effect.

Because experiments are best suited eth-ically and practically to the study of healthbenefits, not hazards, experiments in envi-ronmental epidemiology would usually belimited to the study of preventive interven-tions. Furthermore, it is generally impossi-ble or infeasible to randomize subjectsindividually. The only practical alternative,therefore, is to randomize by group, wherethe group might be a city, school, work site,etc. (29). The major limitation of grouprandomization is some within-group depen-dence (correlation) of the outcome variable,which reduces precision and power (30,31).Thus, the effective sample size falls betweenthe number of randomized groups and thetotal number of subjects (see Prentice andThomas, this issue).

As an example, consider the hypothesisthat the intake of fluoride ions in drinkingwater has a protective effect on the occur-rence of dental caries in children. Anexperiment might be conducted by ran-domly assigning many water districts (eachwith one fluoride-deficient water supplywithout treatment) either to implementsodium fluoride treatment under the con-trol of the investigators or to continue itscurrent policy of no treatment for the dura-tion of follow-up. Assuming the hypothe-sis were true, we would expect the subsequentincidence rate of dental caries to be lowerin the treated districts than in the untreateddistricts.

Randomization insures a valid compari-son of subjects according to intended treat-ment, i.e., assigned treatment, but notaccording to treatment actually received(16;28). That is, randomization of a suffi-cient number of units (subjects or groups)provides some assurance that the assigned

treatment groups are comparable withrespect to inherent risk. This does not implythat there can be no confounding in a com-parison of randomly assigned groups. Evenwith perfect adherence to treatment assign-ments and no loss to follow-up, assignedgroups might have, by chance, differenthypothetical risks in the absence of treat-ment. Nevertheless, such confounding, if itexists, is equally likely to be positive or nega-tive; conventional confidence-interval esti-mates and p values reflect the possibility ofthis bias, which becomes smaller as the(effective) sample size increases (28). Thisprotection against confounding afforded byrandomization, however, does not apply tolack of adherence or loss to follow-up, bothof which usually do not occur randomly.Furthermore, if some subjects cross overbetween treatments (e.g., residents of a fluo-ridated district obtain their water from non-fluoridated districts), a comparison ofassigned groups will underestimate the truetreatment effect even when the crossover is ran-dom (32). A comparison of compliers withnoncompliers, on the other hand, is essentiallyobservational and therefore prone to bias.

Qwsi-ExpeHments. A quasi-experimentmay be done similarly to an experiment bycomparing two or more nonrandomizedgroups, or it may be done by comparing one ormore groups over time, before versus after theintervention is initiated in at least onegroup. With the latter approach, the com-position of each group may change overtime so that subjects observed before theintervention are not the same subjectsobserved after the intervention.

Returning to the fluoride hypothesis, aquasi-experiment was done in the 1940sand 1950s by comparing two similar,nearby cities in New York State, both ofwhich lacked fluoride treatment before1945. Newburgh started sodium fluoridetreatment in 1945 and continued through-out the 10-yr postintervention follow-upperiod; Kingston continued to use its fluo-ride-deficient water without treatment(33). The investigators found that the rateof decayed, missing, or filled (DMF) teethin children, ages 6 to 12, decreased byalmost 50% in Newburgh but increasedslightly in Kingston.

Because subjects were not individuallyrandomized in this study, it is possible thatchildren in the treated group differed fromchildren in the comparison group withrespect to other risk factors for tooth decay,such as diet. Thus, the investigators' com-parisons might have been confounded.Note, however, that randomization by citywould not have reduced this possible bias


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in the Newburgh-Kingston study, becausethe two assigned treatment groups wouldbe equally noncomparable regardless ofwhich city was assigned fluoride treatment.

Observational Studies. Unlike experi-ments and quasi-experiments, observationalstudies are commonly used to estimate theeffects of exposures hypothesized to be harm-ful, fixed attributes (e.g., race and genotype),characteristics, behaviors or exposures overwhich the investigator has little or no control(e.g., weight, depression, and sunlight expo-sure), and other exposures for which manip-ulation or randomization would be unethicalor infeasible. Observational studies are oftenconducted with secondary or retrospectivedata (instead of primary prospective data)and/or without following individual subjectsfor change in disease status. For example,the fluoride hypothesis could be tested bycomparing the prevalence of decayed, miss-ing, or filled teeth in children who live inareas supplied by fluoridated water with thecorresponding prevalence in children wholive in areas supplied by nonfluoridatedwater. Although such a study would be lessexpensive and easier to conduct than wouldthe previous examples, there are additionalmethodologic problems that could lead tobias or misinterpretations.

The remainder of this artide is devotedto an elaboration of observational studydesigns. In "Basic Observational Designs,"we cover the basic designs in which data ondisease status, exposure status, and allcovariates are collected at the individuallevel; that is, the unit of analysis is the indi-vidual (or body part, such as the tooth oreye). In "Ecological Designs," we coverdesigns in which the unit of analysis is agroup of individuals, such that informationis missing on the joint distributions of keyvariables at the individual level.

Basic Observational DesignsFrequently, hypotheses about environmen-tal risk factors for disease are derived fromanimal studies, dinical observations, reportsof disease clusters, descriptive findings frompopulation surveillance systems, and varioustypes of exploratory studies (e.g., case series,mapping studies, and migrant studies).Formal testing of these hypotheses mostoften proceeds by conducting observationalstudies of the types described in this section.

Basic designs in epidemiology may be clas-sified according to two dimensions: type ofstudy population and type ofsampling scheme(34). First, the study population is longitudi-nal, involving the detection of incident eventsduring a follow-up period; or it is cross-sec-tional, involving the detection of prevalent

cases at one time. Second, the sampling strat-egy involves complete selection of the entirepopulation from which study cases are identi-fied, or it involves incomplete or case-controlsampling of a fraction (<100%) of the non-cases in the population from which study casesare identified. Case-control sampling, there-fore, implies stratification on disease status inthe selection process. Combining these twodimensions results in four basic designs: longi-tudinal studies of a complete population(cohort studies); cross-sectional studies of acomplete population (cross-sectional studies);longitudinal studies with case-control sam-pling (case-control studies with incident cases);and cross-sectional studies with case-controlsampling (case-control studies with prevalentcases). In addition to these basic designs, wealso discuss new developments in genetic stud-ies for assessing gene-environment mteractions(see "Genetic Studies").

Cohort StudyA cohort or follow-up study is a longitudi-nal design of a specified population inwhich exposure status is measured for allsubjects at the start of follow-up (baseline)and possibly during follow-up. The entirestudy population-typically persons whoare free of the index disease at baseline-are followed for detection of all incidentcases or deaths of interest. Thus, the basepopulation in this design is identical to thestudy population.

Cohort studies may be entirely prospec-tive, meaning exposure status and diseaseoccurrence are ascertained for the periodduring which the study is conducted, orthey may be entirely retrospective (histori-cal), meaning exposure status and diseaseoccurrence are ascertained for a periodbefore the study begins. Retrospective dataare usually obtained from the subject'srecall of past events or from abstractedrecords. Many cohort studies combineboth data-collection procedures; e.g., thefollow-up period for detecting the diseasestarts before the study and continuesthroughout the study period. Althoughretrospective studies are generally much lessexpensive and time-consuming, prospectivestudies can be designed to collect moreappropriate, complete, and accurate data.

Example. Suppose we want to estimatethe possible effect of prenatal exposure topassive smoke (not maternal smoking) onthe risk of lower respiratory disease duringthe first 3 years of life. We might identifya large group of nonsmoking pregnantwomen and interview them just beforedelivery about their exposure to passivesmoke during pregnancy and about other

risk factors for the disease. The assessmentof passive smoking would involve measur-ing exposure at home, work, and elsewherewith an attempt to quantify the number ofsmokers, cigarettes, and/or exposure timefor each woman by trimester. Then eachneonate would be followed by periodicexaminations and parental reports of symp-toms to his or her third birthday. By estab-lishing a standard set of criteria for diagnosingnew cases of lower respiratory disease andby categorizing the passive-smoke exposureinto two or more categories, we can com-pare the 3-year risk of disease by exposuregroup. In this hypothetical example, theexperience of each subject contributes to asingle exposure group. Since subjects arenot randomized to exposure groups, it isimportant to control analytically for otherrisk factors that are associated with expo-sure status in the study (base) population.For example, we might want to control forthe child's exposure to passive smoke athome; if other family members smokedduring the mother's pregnancy, they arealso likely to have smoked during thechild's first 3 years of life. On the otherhand, we should probably not control forbirth weight even if it is a risk factor for thedisease, because prenatal smoking affects birthweight. Thus, provided low birth weight is arisk factor for lower respiratory disease duringthe first three years of life, low birth weight islikely to be an intermediate variable in thecausal pathway between prenatal exposure topassive smoke and the disease.

Strengths of a Cohort Design. Theprospective cohort study is the observa-tional design that is most similar to anexperiment. The major strengths of thisdesign derive from the fact that diseaseoccurs and is detected after subjects areselected and after exposure status is mea-sured. Thus, we can usually be confidentthat the exposure preceded the disease (i.e.,there is no temporal ambiguity). This fea-ture is particularly important when diseasecan also influence exposure status (e.g.,persons with asthma moving to drier, less-polluted areas). Well-designed retrospec-tive cohort studies also lack temporalambiguity of cause and effect.

Another major strength of the cohortdesign is the usual lack of selection biasthat threatens other basic designs (2).Disease status cannot, in principle, influ-ence the selection of subjects except, per-haps, in poorly designed retrospectivecohort studies. Sometimes researchers,ignoring this principle, propose randomsampling to reduce bias. In fact, randomsampling in a cohort study, unlike random


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assignment, does not prevent or necessarilyreduce epidemiologic bias in effect estima-tion; i.e., random sampling generally doesnot improve comparability between expo-sure groups. It does, however, make thestudy population representative of a larger,well-defined source population (samplingframe), which may make one's findingsmore generalizable. For example, supposewe initiated a prospective cohort study oflung cancer by mailing questionnaires to arandom sample of 500,000 adults living ina given region served by population cancerregistries. The questionnaire would requestinformation on previous cancer diagnoses,exposure variables, and other risk factorsfor lung cancer. Following responses by100,000 selected residents, the cancer reg-istries would be used to identify all newcases of lung cancer diagnosed amongrespondents during the subsequent 5 years.Even though the 100,000 respondents willdiffer in many ways from the 400,000 non-respondents, these differences will notcause epidemiologic bias in effect estima-tion. Nevertheless, the exposure effectobserved for respondents (the base popula-tion) may not be generalizable to the popu-lation of nonrespondents. One possiblereason for this lack of generalizability isthat respondents and nonrespondents differon the joint distribution of one or moreeffect modifiers.

As we will see in the next two sections,the same level of nonresponse in a cross-sectional or case-control study that weassumed in the above cohort examplemight seriously threaten the validity ofeffect estimation. Thus, unlike cohort (orrandomized) studies, nonresponse in otherbasic designs can easily introduce selectionbias because study cases have alreadyoccurred when subjects are selected. Asnoted in "Sources of Epidemiologic Bias,"selection bias is most likely to be problem-atic when the investigator does not identify thebase population from which study cases arose(as in cross-sectional studies and certaincase-control studies).

Weaknesses of a Cohort Design. Apotential weakness of cohort designs is theloss of subjects to follow-up due to deathfrom other diseases, lack of participation,or migration. Unlike subject selection, lossto follow-up can easily bias effect estima-tion if attrition is associated with diseaserisk to a different extent for exposed andunexposed groups (2,35). Unfortunately,we can neither rule out nor confirm suchbias by comparing lost subjects and fol-lowed subjects with respect to baselinecharacteristics (including risk factors) (35).

At best, baseline similarities between lost andfollowed subjects only suggest that loss to fol-low-up is probably not a major threat tovalidity, especially ifthe attrition rate is low.

Perhaps the major practical limitation ofa cohort design, especially prospective stud-ies, is its inefficiency for studying rare out-come events, which is what most diseases arein nonclinical populations. Because expo-sure status and other covariates must beobserved at the start of follow-up in theentire study population, a rare disease wouldmean that most subjects will remain non-cases. Comparing a small number of caseswith a large number of noncases is statisti-cally and economically inefficient because ofthe diminishing marginal return from addi-tional noncases. Assuming a fixed samplesize, therefore, it is more efficient to study adisease with an expected risk of30% than tostudy a disease with an expected risk of 1%;the former will result in more precision andpower for estimating and testing the expo-sure effect. Moreover, substantial increasesin the sample size to compensate for too fewexpected cases is often impractical or impos-sible, especially when the size of the exposedpopulation available for study is limited.

Time-Dependent Exposures. In conven-tional analyses of cohort-study data, exposurestatus and other covariates are usually treatedas fixed variables measured at baseline. Yetthe instantaneous and cumulative level ofmost environmental exposures changes duringthe follow-up period. Consequently, thegreater the change and the longer the follow-up, the less appropriate are conventionalmethods of analysis. A common solution tothis problem is to measure average exposure,duration of exposure, or cumulative exposurebefore and during the follow-up period; thenthese variables are analyzed like the simple base-line exposure variable, as possible (fixed) predic-tors of disease occurrence. Unfortunately, thisapproach also has methodologic problems:a) if the follow-up period for detecting diseaseoverlaps the period during which exposurechange is measured, the temporal relationshipof an exposure-disease association is ambigu-ous. We may not know whether exposurechanges preceded disease occurrence or diseasepreceded changes in exposure level. b) If thelevels of exposure and/or other risk factorschange over time, the associations between theexposure and these covariates also can change;then the amount of confounding of the esti-mated exposure effect will change. The ana-lytic method described above, therefore, willnot, in general, eliminate confounding due tothese risk factors (even when there is no mis-dassification). c) When an extraneous riskfactor affects subsequent exposure status and is

affected by previous exposure status, that riskfactor can be a confounder and an intermedi-ate variable simultaneously (36,37). Forexample, suppose we want to estimate theeffect of exposure duration on mortality froma specific disease. If early symptoms of thedisease lead to termination of exposure, thenearly symptoms, which is a risk factor for dis-ease mortality, is both a confounder and anintermediate variable of the exposure-diseaserelationship. Consequently, standard meth-ods of analysis will generally lead to a biasedestimate ofthe exposure effect, whether or notone adjusts for the risk factor.A statistical solution to the above prob-

lems was recently developed by Robins(36,37) who treats the prolonged or chang-ing predictor variables as time-dependentcovariates for which repeated observationsare collected during the follow-up. Themethod involves estimating causal parame-ters for hypothetical exposure experiences ofthe study population (15). For example, wemight want to compare the outcome risk forall subjects had they remained exposedthroughout follow-up with these subjectshad they remained unexposed, controllingfor confounders at the start of each interval(time stratum).

Cros-Secton StudyA cross-sectional design involves a singleascertainment of disease prevalence in astudy population that is usually sampledrandomly from a single source population.In this sense, the source population is thatlarger group of individuals who are desig-nated by the investigator as being eligiblefor inclusion in the study. Generally, in across-sectional study, we do not know howlong prevalent (existing) cases have had thedisease, nor can we identify the base popu-lation (at risk) from which the study casesarose. Exposure data on time-dependentvariables are usually measured retrospec-tively to allow for expected variations in diseaselatency (before detection) and duration ofexpression (after detection).

The statistical analysis of cross-sectionaldata typically resembles the analysis ofcohort or case-control data. Instead ofcomparing disease risks for exposed andunexposed groups, we compare diseaseprevalences (P), as in a cohort study, or wecompare the prevalence odds (P/(1-P)), asin a case-control study (see "Case-ControlStudy"). Under certain conditions or assump-tions, the prevalence ratio or prevalenceodds ratio is approximately equal to theratio of incidence rates or risks (i.e., thecausal parameter of interest) (2,38). Forexample, disease prevalence in a population


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is a function of both incidence and theduration of disease. If the mean durationof disease (from onset to recovery or death)is known to be identical for exposed andunexposed cases, we can be more confidentthat the prevalence odds ratio approximatesthe incidence rate ratio.

Example. Suppose we want to estimatethe possible effect of prenatal exposure topassive smoke (as in "Cohort Study") onbirth weight, categorized for convenienceinto low (<2500 g) and normal. We iden-tify all live births delivered in one hospitalduring a given period (the source popula-tion); then we take a random or quasi-ran-dom sample (e.g., every third birth). Byobtaining exposure data retrospectivelyfrom mothers near the time of delivery, wecan compare the prevalence of low birthweight for infants prenatally exposed andunexposed to passive smoke, controllinganalytically for confounders (e.g., maternalage, maternal smoking, and prenatal care).

Even though births may be regarded asincident events, the infant's weight at birth is aprevalence measure, because we do not knowthe size of the base population. The causalparameter ofinterest is a hypothetical compari-son of retarded development between fetusesexposed to passive smoke and those fetuses hadthey not been exposed. Not only can we notobserve this hypothetical condition of exposedfetuses being unexposed, but we do not (orcannot) follow the base population; the preva-lence of low birth weight is simply the endresult ofthat hypothetical follow-up.

Strengths ofa Cross-Sectional Design.Because there is no follow-up, cross-sectionalstudies are less time-consuming and costlythan prospective cohort studies. It is also fea-sible to examine many exposures and diseasesin the same study, which makes this designuseful for screening new hypotheses. In addi-tion to causal inference, cross-sectional stud-ies are important descriptively in healthadministration, planning, and policy analysis;information on disease prevalence is oftenrequired to assess the need and demand forhealth services and to evaluate interventionprograms in specific target populations (2).

Weaknesses ofa Cross-Sectional Design.A major methodologic limitation of manycross-sectional studies for making causalinferences is temporal ambiguity of causeand effect. Because we usually do not knowthe duration of the disease in prevalent casesand because exposure status is measured atthe same time as disease status, often wecannot determine that exposure (or a certainaccumulation of exposure) preceded diseaseoccurrence. One approach for minimizingthis problem is to collect retrospective expo-

sure data and information on previous med-ical diagnoses and the onset of symptomsassociated with the disease under study.Not only may this approach be very unin-formative for temporally linking exposureand disease, but it is also likely to worsenanother potential problem, measurementerror. Reliance on retrospecive data increasesthe likelihood and magnitude of measure-ment errors, which generally leads to infor-mation bias. Furthermore, because all dataare collected after disease has occurred, it isvery possible for the error in measuring onevariable to be related to the other variable(differential misclassification) or to error inmeasuring the other variable (correlatederrors). Such possibilities are particularlylikely in survey research and make potentialinformation bias severe and unpredictable.

When cross-sectional studies are con-ducted without random sampling, theyoffer little opportunity for making statisti-cal inferences about descriptive, popula-tion-specific parameters, e.g., the prevalenceof a disease in a specified source population(28). The lack of random sampling mayalso worsen the potential problem of selec-tion bias in effect estimation, which wouldbe difficult to rule out a priori or to correctin the analysis. Even with random sam-pling, however, disease status or exposurestatus can influence the selection of sub-jects differentially by category of the othervariable. For example, exposed cases maybe less likely than others to be selected forstudy, perhaps because new exposed casesare less likely to survive than new unex-posed cases (i.e., selective survival) orbecause exposed cases are less likely to enterthe specified source population such as ahospital (i.e., Berkson's bias) (2). Similarly,selection bias can result from the differen-tial participation of selected subjects (i.e.,response bias).

Case-Control StudyCase-control studies are distinguished fromother basic designs by their sampling strat-egy: The investigator selects only a fractionof noncases (controls) from the populationfrom which the cases were identified(2,3,5,34,39). Sometimes this population isnot the true (primary) base population (outof necessity or convenience), and occasion-ally controls are assembled without regardfor the identification of cases. The designmay be longitudinal, involving incidentcases, or cross-sectional, involving prevalentcases. In both types, the investigator estab-lishes the ratio of controls to cases, whichdoes not depend directly on the frequencyof disease in the population. As in cross-sec-

tional studies, exposure data on time-dependent variables are generally measuredretrospectively to account for expected varia-tions in disease latency.

Estimation ofEffect. Unless the crudedisease rate or the size of the base popula-tion is known, we cannot estimate the riskor rate of the disease in the exposed andunexposed populations. Nevertheless, wecan estimate the effect of the exposure ondisease by calculating the exposure oddsratio, which computationally is similar tothe prevalence odds ratio in a cross-sec-tional study (2,3,19,20). For this estima-tion of effect to be valid, however, thecontrols must be representative of the basepopulation that gave rise to the study cases.In this context, representative means hav-ing a similar distribution on other diseaserisk factors and indicators of disease detec-tion. The best method for making the con-trols representative in this way is to samplethem randomly (with or without matching)from the base population (see below).

Matching. As in any observationalstudy, the investigator should control ana-lytically for confounders by stratification ormodel fitting. Intuitively, it would appearthat one method for achieving this controlis to match controls to cases on extraneousrisk factors (i.e., making controls similar tocases on the joint distribution of these riskfactors). In a case-control study, however,it is not the matching alone that controlsfor the confounding effects of the matchingvariables; rather, stratification in the analy-sis eliminates this bias (1-6). In fact, thenet effect of matching in case-control stud-ies (but not in cohort studies) is to intro-duce selection bias that must be controlledin the analysis. Thus, if the matching isignored in the analysis, the effect estimatewill usually be biased (2,4,14).

The potential advantage of matching inthe selection of subjects is that it allows theinvestigator to control for confoundersmore efficiently than if matching is notused (1-6). Yet, in this regard, matchingcan be counterproductive if one matches ina case-control study on strong correlates ofexposure in the base population that arenot risk factors (or proxy risk factors) forthe disease. This type of overmatchingresults in a decrease in statistical efficiency(i.e., less precision for a given number ofcases and controls) (1-6). The conditionsfor overmatching, however, are very differ-ent in cohort studies in which unexposedsubjects are matched to exposed subjects(40). Matching can also be economicallycounterproductive for achieving a certainminimal precision if it costs more to match


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than to increase the sample size withoutmatching (41).

Population-Based Case-Control Study.In a population-based or hybrid case-con-trol study, controls (noncases) are sampleddirectly from the base population that gaverise to the cases (39,42). When this designinvolves the follow-up of a large dynamicpopulation, such as residents of a state, iden-tification of new cases is usually based ondata collected through a population registry.The validity of effect estimation depends onthe completeness and accuracy of case ascer-tainment and on careful description of thebase population. When the design involvesthe follow-up of individuals in a fixedcohort (e.g., as a part of a clinical trial orcohort study), identification of new cases isdone by exams, interviews, or questionnairesadministered periodically to each individ-ual in the cohort during the follow-up.This latter strategy is npw called a nestedcase-control study but also has been called asynthetic case-control study (43).

There are three alternative methods forselecdng controls in a longitudinal, population-based case-control study a) In density sam-pling, controls are selected longitudinallythroughout the follow-up. Typically, theyare individually matched to cases on time ofeach case's diagnosis or identification andpossibly other factors; i.e., each control isknown to be at risk (disease-free) at the timeits matched case was first identified as dis-eased. An advantage of time matching isthat exposure status is measured at about thesame time for all subjects in each matchedset (19). b) In cumulative sampling, allcontrols are selected at the end of the follow-up period during which cases are identified.Both cumulative- and density-samplingmethods can be used even when controls arenot selected directly from the base popula-tion. c) In case-base or case-cohort sam-pling, all controls are selected from the fixedbase population at the start of the follow-up(42,44,45). An advantage of this method isthat one control group can be used to studymultiple diseases, provided that prevalentcases of each disease are excluded from theanalyses involving that disease. In bothcase-base and density sampling, it is possiblefor a selected control to subsequently developthe disease and become a case in the study.

Example. Suppose we want to estimatethe possible effect of prenatal exposure topassive smoke (as in previous examples) onthe risk of sudden infant death syndrome(SIDS). Using hospital records and birthcertificate information, we identify a largenumber of live births occurring in a givenregion during a certain period. Then this

base population is followed prospectively,using hospital records and/or a populationregistry to identify all infant deaths. Foreach diagnosed and confirmed case ofSIDS, we randomly select two live controlsmatched to the case on age, race, and dateof the case's death; thus, controls are den-sity sampled from the follow-up experience(risk set) of the base population of livebirths. As soon as possible after case detec-tion, we interview the mothers of all sub-jects to collect data on prenatal exposure topassive smoke and other covariates.

Proportional (Case-Control) Study. Aproportional study is a special type ofcase-control study in which selected con-trols have developed or died from diseasesother than the index disease under study(2). By definition, therefore, this is not apopulation-based design, since controls(especially deaths) may not be representa-tive of the base population from whichstudy cases arose. In a proportional mor-bidity study, both cases and controls areselected from a dinical population such asa hospital, clinic, physician's practice, orscreening program. Controls are selectedbecause they have other conditions or symp-toms; thus, and they are likely to differ fromthe base population of cases in ways that affectdisease occurrence or detection. This situationwill usually occur when the exposure is a riskfactor for those comparison diseases makingup the control group. For example, we wouldobtain a severely biased estimate of the smok-ing effect in a hospital-based, case-controlstudy if controls were selected from emphy-sema patients because smoking is a strong riskfactor for emphysema.

Deaths comprise the entire populationof a proportional mortality ratio (PMR)study. A group of deaths from the indexdisease (cases) is compared with a group ofdeaths from other diseases that mightinclude selected comparison disease(s) orall other causes of death. Typically, allstudy deaths are identified retrospectivelyfrom the follow-up of a single population,such as persons living in a certain region oremployed by a certain company during agiven period. Although study deaths areincident events often identified from adefined base population, the outcome vari-able in this design is prevalence of diseaseat death; we do not have the proper denomi-nator to estimate the disease-specific mortalityrate in any (base) population. Furthermore,exposure data are not obtained for the basepopulation but for study deaths only.

In the conventional proportional mortal-ity study, comparison deaths are all othercauses of death occurring in the population.

The traditional method of analysis is tocompute the PMR, which is the proportionof exposed deaths resulting from the indexdisease divided by the proportion of unex-posed deaths resulting from the index dis-ease (6). Altematively, the data are analyzedas in a case-control study, the researcher com-putes the mortality odds ratio (46,47). Animportant advantage of the alternativeapproach is that the comparison (control)group might be selected to indude only thosediseases thought to be unrelated to exposurestatus. This design strategy, which also shouldbe used in a proportional morbidity study,can help reduce selection bias by makingthe comparison group more representative ofthe base population. Another advantage is thatit allows use of the many analytic techniquesdeveloped for case-control studies (48,49).

Strengths of a Case-Control Design.The major advantage of the case-controldesign over other basic designs is its effi-ciency for studying rare diseases, especiallydiseases with long latent periods. A greaterproportion of study costs for collectingexposure and covariate data can be devotedto cases rather than expending most availableresources on noncases. Thus, given a fixedsample size, case-control sampling in a studyof a rare disease enhances the precision andpower for estimating and testing the exposureeffect. In addition, some case-control stud-ies, particularly proportional mortalitydesigns, tend to be relatively inexpensiveand feasible because they can be based onreadily available data sources.

Weaknesses ofa Case-Control Design.A key issue in the design of case-controlstudies is the method and procedures forselecting controls. Ideally, we would liketo make each study population-based, suchthat every new case occurrence in a well-defined base population is immediatelyidentified by the investigators and controlsare sampled randomly from the base popu-lation. In practice, however, this goal isnot so easily accomplished, especially whenthe base is a large, dynamic population thatcannot be examined periodically. Evenpopulation surveillance and registry sys-tems, when they exist, are likely to be veryincomplete for many diseases, such asprostate cancer, Alzheimer's disease, andischemic heart disease. If exposed cases aremore likely or less likely to be detected orreported than unexposed cases, the result-ing effect estimate will be biased. In acohort study, this detection problem wouldmanifest as differential disease misclassifica-tion bias; but in a case-control study, thedetection problem produces a form ofselection bias that might involve no disease

29Environmental Health Perspectives SupplementsVolume 101, Supplement 4, December 1993


misclassification in the total sample and,therefore, cannot be corrected after subjectselection (50). To prevent such detectionbias, the investigator might select controlswho, purportedly, underwent the samedegree of medical surveillance as did studycases (51) (e.g., persons screened for thedisease or patients treated for other relatedconditions). Unfortunately, this approachcould introduce another problem by selecingfor the control group individuals with otherexposure-related conditions (see the discussionof proportional morbidity studies). The endresult might be, for example, to overcompen-sate for potential detection bias, producing netbias in the opposite direction. In general, inthe absence of perfect population-based meth-ods, investigators must select controls to reflectthe expected magnitudes of various potentialselection problems.

When there is relatively little variabilityof exposure in the base population, weexpect imprecise estimation of the exposureeffect, even if the exposure is a strong riskfactor for the disease. Although such inef-ficiency is usually quite apparent in cohortstudies, it may not be so apparent incase-control studies, especially when theinvestigator does not know the exposuredistribution in the base population. Forexample, if environmental exposure levelsare high throughout the region of the basepopulation, a comparison of cases and con-trols would result in an unstable estimateof effect and low power. As in cohort stud-ies, the problem is not one of bias. Limitedvariability of exposure is likely to occurwhen exposure status for individual sub-jects is measured ecologically by assigningto each subject the exposure level observedfor the area in which that subject lives orworks. Other problems accompanyingecologic measurement are discussed in"Ecologic Designs."

Two-Stage Designs. Just as cohortstudies are inefficient for studying rare dis-eases, case-control studies are inefficientfor studying rare exposures. When bothdisease and exposure are rare, therefore, anybasic design might require a very large sam-ple size to ensure adequate power. Onesolution to this problem is a two-stagedesign: stage 1 is a basic design in whichdata are collected on exposure and diseasevariables only; in stage 2, covariate dataand possibly more refined exposure data(with less measurement error) are collectedon separate random samples of exposedcases, exposed noncases, unexposed cases,and unexposed noncases, all of which areidentified from stage 1 results (52,53).Sampling fractions for stage 2 are set larger

for those exposure-disease groups that con-tain fewer subjects in stage 1. Thus, theinvestigator can obtain approximately equalnumbers of the four exposure-diseasegroups in stage 2. Stage 1 results are usedto estimate the crude (unadjusted) expo-sure effect, and stage 2 results are used toestimate the effect adjusted for covariatesand possibly a more refined exposure effect.The analysis of stage 2 data considers thesampling fractions (52-56). The two-stage design is also advantageous when thecost of obtaining covariate data is large rel-ative to the cost of obtaining exposure anddisease data or when covariate data aremissing on a majority of subjects (52,54).

Case-Crossover Design. A standardcrossover design is an experiment or quasi-experiment in which each subject receivesboth the experimental and control treat-ments at different times (i.e., each subjectserves as his or her own control) (57). Suchdesigns are seldom used in environmentalepidemiology because manipulation oftreatment status (with or without random-ization) is usually unethical or infeasibleand because the outcome is usually a rareevent. Recently, Maclure (58) proposed anobservational analogue of the crossoverstudy called the case-crossover design,which may be regarded as a special type ofpairwise-matched, case-control study.This type of design can be used to estimatethe possible transient effect of a brief expo-sure (e.g., coffee drinking) on the subse-quent occurrence of a rare acute-onsetdisease (e.g., myocardial infarction) that ishypothesized to occur within a short timeafter exposure (i.e., during the effectperiod). All subjects are newly detectedcases that serve as their own controls. Thatis, for each case, the observed odds of beingexposed during the effect period (e.g., onehour before disease onset) is comparedwith the expected odds of being exposedduring any random period of the sameduration (assuming no exposure effect).The expected exposure odds is estimatedfrom the subject's report of his usual expo-sure frequency before disease occurrence.For example, if a person drinks coffee twiceeach day and the effect period is 1 hr, theexpected odds of exposure during any 1-hrperiod is 1/11. Thus, we would expectthat, for every 12 cases who drank coffeetwice each day, one case would haveoccurred by chance within 1 hr of expo-sure. Maclure recommends using standardmethods of matched analysis for person-time (cohort) data to combine data fromall cases; however, this approach needs fur-ther development to handle the temporal

autocorrelation of outcome status (i.e., acase is either exposed during the effectperiod or unexposed, but it cannot be both).Although the case-crossover design has notyet been used to examine the possibleshort-term effect of an environmentalexposure, this type of study is feasible ifwecan measure such exposures.

Gene6c StdyThe study of variation among individuals orgroups in their sensitivity to environmentalagents is one of the aims of environmentalepidemiology. Such variation might be dueto differences in host characteristics, indud-ing genetic factors, or to interactions withother exposures. A complete survey of themethods used to study the genetic determi-nants of disease would be beyond the scopeof this report; instead, we will focus on theapproaches that might be used to address theissue ofgene-environment interactions.

Three basic types of information mightshed light on the genetic component ofsuch interactions: a classification of thesubjects' genotypes at a major locus for dis-ease susceptibility; some observable hostcharacteristic (phenotype) that is geneti-cally determined and linked with the geno-type that was responsible for sensitivity; orfamily history as a surrogate for genetic (orshared environmental) influences. Thechoice of study design will depend uponwhich of these is sought.

The first is the most powerful approach,and its feasibility will grow as more andmore genes are identified and assays forthem become available. If the genotype isobservable, it can be considered simplyanother risk factor and any of the basicdesign and analysis strategies used in epi-demiology are applicable. For example,Caporaso et al. (59) reported a case-controlstudy of lung cancer, in which the rate ofmetabolism of the antihypertensive drugdebrizoquine was taken as a phenotypicmarker for a gene in the cytochrome P450system that is responsible for metabolism ofcarcinogens. It was shown that intermediateand high metabolizers were at higher risk oflung cancer overall and that there was an inter-action between metabolic rate and exposure tooccupational carcinogens and smoking. In thisexample, the genotype was not observeddirecdy but inferred from the phenotype, butrecent advances in molecular genetics, such asthe use of restriction fragment length poly-morphism, are making direct observationincreasingly feasible.

Identifying host characteristics thatinteract with environmental exposures canbe done in essentially the same way. A


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familiar example might be skin color as amarker for sensitivity to sunlight in theproduction of melanoma. No extensions ofstandard epidemiologic methods would beneeded to address this question. The onlysubtlety in this case arises when the genedetermining the host characteristic is not thedisease susceptibility locus but only linkedto it (i.e., nearby on the same chromosome).A particular marker allele might be associ-ated with the disease in one family and a dif-ferent allele in another family-, but in bothfamilies, the marker and the disease wouldbe inherited together. This possibilityrequires family data and the techniques oflinkage analysis. To date, such analyses havebeen applied only to the study of geneticeffects without reference to the environmen-tal covariates, but statistical techniques thatwould assess such combined effects recendyhave become available (60).

Before trying to identify a specific majorgene that is related to sensitivity to environ-mental exposures, one should assess whetherthere is any evidence that such sensitivity hasa genetic basis. This also requires collectionof family data, but unlike the standard analy-ses aimed at examining the main effect ofgenetics, one would also want to examineinteractions between family history and envi-ronmental exposures. Geneticists commonlyassemble a small number of very large pedi-grees, sometimes selected to maximize thechances that a major gene is operating in thefamilies, and subject them to segregationanalysis to study the mode of inheritance.Again, these analyses seldom account forenvironmental covariates and interactions,although such methods are now available. Incontrast, epidemiologists begin with a largepopulation-based series of cases and controlsand restrict attention to the first- and some-times second-degree family members. Theiranalyses usually are limited to a simple familyhistory covariate (e.g., presence ofan affectedmember, number of affected members, etc.)in standard multivariate risk-factor models,possibly but seldom including interactionswith environmental covariates. Susser andSusser (61) have discussed two basicapproaches to such data: in the case-con-trol approach, cases are compared with con-trols in terms of their family histories; in thecohort approach, the incidence of disease inthe exposed (case) families is compared withthe incidence in unexposed (control) fami-lies. Either approach could easily beextended to incorporate environmentalcovariates and their interactions with fam-ily history. The only difference is that thecohort approach requires covariate data onall of the family members, whereas the

case-control approach requires data only onthe originally sampled cases and controls.Clearly, the cohort approach is more infor-mative, but the conditions under which theadditional effort warrants the gain in infor-mation about gene-environment interactionshave not been investigated.

The two major design issues to beaddressed in such studies are the method ofascertainment of families and the informa-tion to be collected on family members.The former has been discussed at greatlength in the genetics literature. The basicproblem is that if families are ascertainedthrough affected probands, families with mul-tiple cases will tend to be overrepresented.Therefore, various corrections for ascertain-ment are applied in the standard methodsof genetic analysis. The relevance of theseapproaches to the epidemiologic designsfor gene-environment interactions requiresfurther research. Often, only very limitedinformation is collected about family his-tory in epidemiologic studies. The mini-mal information should be an enumerationof all affected family members togetherwith the sex and age of each family mem-ber at risk; as discussed above, informationon major risk factors for all family mem-bers at risk may also be desirable. Becauselarger and older families are likely to havemore familial cases, the presence or num-ber of familial cases is not suitable as a fam-ily history covariate. Moreover, expressingthe number affected as a proportion doesnot solve the problem because multiplecases in large families are more informativethan single cases in small families. A moreappropriate comparison is between theobserved number of familial cases and theeqxcted number based on the person-time atrisk, in which the comparison is adjusted forage, sex, and other important risk factors (62).

Ecologic DesignsAn ecologic or aggregate study is one inwhich exposure levels of individuals are notlinked to disease occurrence of those indi-viduals. The net result is that the unit ofstatistical analysis is usually the group, typi-cally persons living in a geographic area suchas a census tract, county, or state. For eachgroup or region, therefore, we know theaverage exposure level or distribution andthe disease rate, but we do not know thejoint distribution of these two variables.Given a dichotomous exposure, for example,we would not know the numbers of exposedand unexposed cases in each group. Thus,we cannot estimate the exposure effectdirectly by comparing the disease rate forexposed and unexposed populations.

Ecologic designs are therefore incom-plete (2) in the sense that they lack certaininformation ordinarily contained in thebasic designs. As noted in "Problems inEnvironmental Epidemiology," the pri-mary reason for this missing information inenvironmental epidemiology is our inabil-ity or lack of resources to accurately mea-sure environmental exposures in largenumbers of individuals. Thus, the wide-spread use of ecologic designs in environ-mental epidemiology reflects a fundamentalproblem of exposure measurement. Inaddition, ecologic studies represent aninexpensive design option for linking avail-able data sets or record systems, even whenexposures are measured at the individuallevel. The appeal of this alternative is thataggregate summaries of many exposures,induding sociodemographic and other censusvariables, are often available for the sameregions that are used to summarize morbidityand mortality data.

With the inclusion of covariate data inan ecologic study, the analysis may be onlypartly ecologic. This condition occurswhen the joint distribution of two or more,but not all, variables is known withingroups. For example, suppose we want toexamine the possible effect of radon expo-sure on lung cancer incidence, controllingfor age (the covariate). Although we mightknow the age distribution of all new casesand all persons at risk within each county(from tumor registry and census data), wewould usually not know the within-countyassociation between radon exposure andthe other two variables. Sometimes datasets like this are analyzed with the individ-ual as the unit of analysis, where each indi-vidual is assigned the average radon exposurelevel that was measured for the region inwhich he or she lives. Such ecologic measure-ment of exposure means that there is likely tobe substantial error in measuring the individ-ual's exposure to radon, which could result ininformation bias of effect estimation.

Types ofEcologic StudiesEcologic studies may be classified into fivedesign types that differ in several ways,including methods of subject selection andmethods of analysis (2,63).

Exploratory Studies. In exploratoryecologic studies, we compare the rate ofdisease among many contiguous regionsduring the same period, or we compare therate over time in one region. In neitherapproach are exposures to specific environ-mental factors measured (for individuals orgroups). The purpose is to search for spa-tial or temporal patterns that might suggest



an environmental etiology or more specificetiologic hypotheses.

The simplest type of exploratory studyof spatial patterns is a graphical comparisonof relative rates across all regions (i.e., map-ping study), possibly accompanied by a sta-tistical test for the null hypothesis of nogeographic clustering (64). In mappingstudies, however, a simple comparison ofestimated rates across regions is often com-plicated by two statistical issues. First,regions with smaller numbers of observedcases show greater variability in the estimatedrate; thus, the most extreme rates tend to beestimated for those regions with the fewestcases. Second, nearby regions tend to havemore similar rates than do distant regions (i.e.,positive autocorrelation). A statistical methodfor dealing with both complications involvesempirical Baye' estimation of rates using anautoregressive spatial model (65).

In certain exploratory studies of spatial pat-terns, regions are characterized in terms ofgeneral ecologic indicators such as degree ofurbanization (urban versus rural), degree ofindustrialization (agricultural versus nonagri-cultural), population density, socioeconomicstatus, and ethnic diversity. The analysis ofthese data usually involves comparisons ofregions grouped by one or more ecologic indi-cators. This approach resembles the statisticalmethods used in multiple-group studies (see"Interpretation of Results").

An exploratory ecologic study was con-ducted by Mahoney et al. (66), who com-pared age-standardized mortality ratios forcancers, by sex, among all cities and townsin New York State (exclusive of New YorkCity) between 1978 and 1982. By group-ing these regions by quintile of populationdensity, they examined the associationsbetween density and deaths from all cancersites and selected sites, by sex. They foundlinear associations between increasing pop-ulation density and total cancer mortalityin both men and women. Because popula-tion density may reflect various risk factorsfor different cancers, the authors acknowl-edge that their findings are consistent withseveral alternative explanations.

An exploratory study of temporal pat-terns is generally done by comparing dis-ease rates for a geographically definedpopulation over a period of at least 20years. A common statistical or graphicalapproach for analyzing such longitudinaldata is cohort analysis (not to be confusedwith the analysis of data from a cohortstudy) (2). The objective of this approachis to estimate the separate effects of threetime-related variables on disease occur-rence: age, period (calendar time), and

birth cohort (year of birth). Because of thelinear dependency of these three variables,there is an inherent statistical limitation(identification problem) with the interpre-tation of cohort-analysis results. The prob-lem is that each data set has alternativeexplanations with respect to the combina-tion of age, period, and cohort effects. Theonly way to decide which interpretationshould be accepted is to consider the find-ings in light of other (prior) knowledge ofthe disease and its determinants.A cohort analysis was conducted by Lee

et al. (67) on melanoma mortality amongwhite males living in the United Statesbetween 1951 and 1975. They concludedthat the apparent increase in the melanomamortality rate during that period was dueprimarily to a cohort effect. That is, per-sons born in more recent years carried withthem throughout their lives a higher mor-tality rate than did persons born earlier. Ina subsequent review paper, Lee (68) specu-lates that the cohort effect might reflect theimpact of changes in a major risk factoroperating during youth, such as sunlightexposure or burning.

Space-Time Cluster Study. Space-timeclustering refers to the interaction betweenplace and time of disease occurrence, suchthat cases that occur dose in space also occurdose in time (2). Evidence of space-timeclustering may suggest person-to-persontransmission of an infectious agent or theeffects of point-source exposures, dependingon the disease and the cluster pattern. Theanalytic search for space-time clustersrequires special statistical techniques thatmay or may not incorporate informationon the base population and covariates(69,70). Although the unit of analysis forthese methods is usually the individual,space-time cluster studies are classified herewith ecologic designs because closeness inspace and time is a proxy measure for envi-ronmental exposures-or at least the opportu-nity for expsr. Thus, use ofplace and timeinformation is analogous to use of spatial ortemporal indicators in the exploratory study.

Space-time duster analyses may be usedwhen members of a community perceive acluster or excess number of cases of one ormore diseases in their area. This activity isoften motivated by the suspicion that theapparent duster is caused by a specific envi-ronmental exposure, such as chemical waste,pesticides, or electromagnetic fields. Wheninvestigation begins, the first steps are to ver-ify the diagnoses of all reported cases and iden-tify any additional cases in the cluster area,which must be defined. In addition tospace-time duster analyses, the investigators

will probably want to compare the disease ratein the duster-area population with the rate inanother population thought to be unexposed(retrospective cohort study), and they mayconduct a population-based case-control studyto identify risk factors for the disease.

Multiple-Group Study. In a multiple-group ecologic study, we assess the ecologicassociation between average exposure levelor prevalence and the rate of disease amongmany groups or regions. This is the mostfrequently used ecologic design in environ-mental epidemiology. Studies are usuallyconducted by linking separate sources ofdata. For example, census and tumor-reg-istry data might be combined to estimate can-cer rates for all counties in a state; otherstate records or surveys might be used toestimate average exposure levels by county.Statistical methods for estimating exposureeffects in multiple-group studies are dis-cussed in "Interpretation of Results" andby Prentice and Thomas in this issue.

Hatch and Susser (71) conducted a mul-tiple-group ecologic study to examine theassociation between background gamma radi-ation and childhood cancers between 1975and 1985 in the region surrounding theThree Mile Island nuclear plant. Using datafrom a 1976 aerial survey, they estimated theaverage radiation level for each of 69 tracts inthe study region. The results of their analysesshowed a positive association between radia-tion level and the incidence ofchildhood can-cers. The authors were cautious in makingcausal inferences, however, because the largeeffect observed for solid tumors, as well asleukemias, was not expected.

Time-Trend Study. In time-trend (ortime-series) studies, we assess the ecologicassociation between change in average expo-sure level or prevalence and change in dis-ease rate in one geographically definedpopulation. The assessment may be doneby simple graphical displays or by more for-mal statistical techniques (72-75). Witheither approach, however, the interpretationof findings is often complicated by twoissues. First, changes in disease dassificationand diagnostic criteria can produce verymisleading results. Second, the latency ofthe disease with respect to the exposure ofinterest may be long, variable across cases,and/or unknown to the investigator; thus,employing an arbitrary or empiricallydefined lag between the two trends can alsoproduce very misleading results (76).

Darby and Doll (77) compared the trendsof average annual absorbed doses of radiationfallout from weapons testing and childhoodleukemia rates in three European countriesbetween 1945 and 1985. Although the


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leukemia rates varied over time in each coun-try, they found no convincing evidence thatthese changes were attributed to changes infallout radiation.

Mixed Study. The mixed ecologicdesign combines the basic features of themultiple-group study and the time-trendstudy. The objective is to assess the eco-logic association between change in averageexposure level or prevalence and change indisease rate among many groups. Thus,two types of comparisons are made simul-taneously: change over time within groupsand differences among groups.

For example, Crawford et al. (78) eval-uated the hypothesis that hard drinkingwater (i.e., water containing more calciumand magnesium ions) is a protective riskfactor for cardiovascular disease (CVD).They compared the absolute change inCVD mortality rate between 1948 and1964, by age and sex, in 83 British towns.The towns were divided into three groups:a) five had experienced increases in waterhardness; b) six had experienced decreases,and c) 72 had experienced little or nochange in water hardness. In all sex-agegroups, especially for men, the authorsfound an inverse association betweentrends in water hardness and CVD mortal-ity. In middle-aged men, for example, theincrease in CVD mortality was less intowns that made their water harder than intowns that made their water softer.

Interpretaon ofResultsStatistical analysis in a multiple-group studyusually involves fitting the data to a mathe-matical model (see Prentice and Thomas,this issue). The outcome variable is a func-tion of the disease rate in each group; pre-dictors indude the average exposure level orproportion exposed in each group plus otherecologic covariates, the effects of which theinvestigator wants to control. We show in"Control for Covariates" that these covari-ates need not be confounders (i.e., at theindividual level within groups).

Results of the fitted model can be usedto estimate the exposure effect, i.e., thesame causal parameter we would like tohave estimated had the study been con-ducted at the individual level (63,79,80).For example, suppose the exposure variableis the proportion exposed in each groupand there are no covariates. Assuming alinear model, we can use weighted least-squares regression to estimate the slope (b)and intercept (a). The predicted diseaserate in a group that is entirely exposed isthen a + b(l) = a + b, and the predictedrate in a group that is entirely unexposed is

a + b(O) = a; therefore, the estimated rateratio is (a + b)la = 1 + bla. It is importantto note that this estimation procedureimplies extrapolating the results of themodel to both extreme values of the expo-sure variable, either or both of which maylie well beyond the observed range. It isnot surprising, therefore, that different modelforms can lead to very different estimates ofeffect (81). In fact, certain model assumptionsmay lead to rate-ratio estimates that arenegative and thus meaningless.

Ecologic BiasThe use of ecologic data to estimate causalparameters has a major methodologic limi-tation, called the ecological fallacy (82),aggregation bias (83), cross-level bias (84),and ecologic bias (85,86). Ecologic biasrefers, in general, to the failure of ecologicestimates of effect to reflect the true effectat the individual level. Some of this biasmay occur in individual-level studies of thesame population, but some of it is duespecifically to the aggregation of subjectsinto groups. More importantly, the magni-tude of ecologic bias is likely to be more severeand less predictable than is individual-level biasin estimating the same effect (63,81,8687).It is very possible, for example, that an ecologicanalysis of a (true) positive risk factor wouldproduce an apparently protective effect.

The underlying problem of ecologicbias may be regarded as a special form ofinformation bias resulting from within-group heterogeneity of exposure status,which is not captured in the analysis. Forexample, a positive linear relationshipbetween proportion exposed and diseaserate does not necessarily mean that exposedindividuals are at greater risk for the diseasethan are unexposed individuals; rather,unexposed individuals may be at greaterrisk in groups containing proportionallymore exposed individuals. The implicationof this latter explanation is that an individ-ual's group affiliation has an effect on dis-ease occurrence that reflects more than justthe individual's exposure status.A mathematical understanding of eco-

logic bias was first provided for correlationcoefficients by Robinson (88) and laterextended to regression coefficients by Duncanet al. (89). Nevertheless, the conditions forvalid ecologic estimation and the relationshipbetween ecologic bias and other method-ologic issues are still not well understood.Because the results of ecologic analyses areoften used to influence policy decisions, aswell as to make causal inferences, it isimportant for researchers to appreciate thecomplexities of ecologic inference.

Sources ofEcologic Bias. Ecologic bias isoften confused with confounding, perhapsbecause regional differences in disease ratescan be due to variation in the distribution ofextraneous risk factors across regions. Todarify the confusion between these two con-cepts, Greenland and Morgenstem (86;87,90)show that ecologic bias can arise from threedifferent sources.

Within-Group Confounding (At theIndividual Level). The exposure effect maybe confounded within groups (as describedfor nonecologic studies in "Sources ofEpidemiologic Bias"). Thus, if the within-group effect is equally confounded by thesame unmeasured risk factors in every group,we can expect the ecologic estimate of effectto be biased as well. In general, ecologic esti-mates will be biased in this way if the netwithin-group bias across groups (due touncontrolled confounders) is not zero. It ispossible, therefore, for positive confound-ing in certain groups to cancel negativeconfounding in other groups.

The other two sources of ecologic biasare unique to this design and can be under-stood by considering group (or group affili-ation) as a nominal predictor of diseaseoccurrence at the individual level.

Confounding by Group. Ecologic biascan occur when the disease rate in the unex-posed population varies across groups. Sinceaverage exposure level also typically variesacross groups, group is a confounder of theexposure effect at the individual level. Thisset of conditions may occur if one or moreunmeasured risk factors are differentially dis-tributed across groups, even if these risk fac-tors are unrelated to exposure status withingroups and, therefore, are not confounders atthe individual level.

Effect Modification by Group. Ecologicbias can also occur when the exposureeffect varies across groups, i.e., when groupmodifies the effect of the exposure at theindividual level. This condition may resultfrom extraneous risk factors (effect modi-fiers) being differentially distributed acrossgroups or by misspecification of the modelform used to analyze the data. Ecologicbias of this type tends to be more severewhen there is little variability in averageexposure across groups (85), even whenthe effect modification is relatively weakand there is no confounding by group.

Taken together, the above principlesimply that there will be no ecologic bias ifthe disease rate in the unexposed popula-tion and the exposure effect do not varyacross groups and if there is no net con-founding within groups. Unfortunately, itis very unlikely that all of these conditions



will be met in one ecologic study. Althoughsmall departures from these conditions mayresult in substantial bias (81,86), it is alsopossible that there will be little or no biasin certain studies when one or more ofthese conditions are not met.

If every group were completely exposedor unexposed, there would be no ecologicbias attributable to confounding or effectmodification by group. Indeed, if all covari-ates were measured at the individual level,such a study would not be an ecologicdesign. Thus, to reduce ecologic bias, weshould select regions that minimize within-region exposure variation and maximizebetween-region variation (63,81). Onestrategy for achieving these goals is to choosethe smallest unit of analysis for whichrequired data are available (e.g., census tractsor blocks). Unfortunately, certain data areseldom available at this level (e.g., personalbehaviors and biomedical factors), and there isno guarantee that these smaller units are morehomogeneous with respect to exposure status.Furthermore, use of smaller groups mightincrease the problem of migration betweengroups (see "Other Methodologic Problems").

Contol for CovariatIn a study conducted entirely at the indi-vidual level, an extraneous risk factor pro-duces bias (confounding) in effect estimationonly if it is associated with exposure statusin the base population (see "Sources ofEpidemiologic Bias"). In a multiple-groupecologic study, however, an extraneous riskfactor can produce ecologic bias even if it isnot associated with exposure status withinregions (at the individual level) (86,87,90).Such bias occurs typically because the eco-logic association (across regions) betweenthe exposure and risk factor produces con-founding and/or modification of the expo-sure effect by group (see "Ecologic Bias").Conversely, an extraneous risk factor that is aconfounder within regions may not produceecologic bias if the net within-group bias iszero (see "Ecologic Bias") or if the risk factoris ecologically uncorrelated with the exposure.

One method to control for extraneous riskfactors in ecologic studies is to indude predic-tor terms for these risk factors in the model(e.g., the proportion of smokers or the meanfamily income in each region). Unfortunately,even when such covariate data are available forall regions, ecologic adjustment usually cannotbe expected to remove completely the ecologicbias produced by these risk factors. In fact, it ispossible for such ecologic adjustment toincrease bias (86).

The general conditions under whichthe ecologic control for extraneous risk fac-

tors either increases or decreases bias havenot been delineated. Yet, under certainrestrictive conditions, ecologic control forcovariates will produce unbiased estimatesof the exposure effect, provided there areno other sources of bias (e.g., outcome mis-dassification). If the effects of the exposureand the covariate on disease rate are exactlyadditive within every region (i.e., the ratedifference for each variable is constantacross levels of the other variable) and if therate conditional on both predictors isexactly the same in every region, ecologicregression of disease rate on the meanexposure and covariate levels (i.e., multiplelinear regression) will lead to unbiased esti-mates ofboth effects (83,84). Under theseconditions, group affiliation does not con-found or modify the exposure effect at theindividual level. However, as shown byGreenland (81), relatively minor deviationsfrom perfect additivity (linearity) can leadto appreciable ecologic bias because eco-logic rate ratios can be extremely sensitiveto the choice of model form, in contrast toindividual-level estimates. Furthermore,the two conditions noted above are onlysufficient for no ecologic bias to occur; eco-logic bias may be absent when either orboth conditions are not met.

Richardson and Hemon (91) recentlypointed out that there is another set ofconditions for which ecologic control ofcovariates is possible. If a) the exposureand covariates are uncorrelated withinregions, b) their effects on disease are mul-tiplicative (i.e., the rate ratio for each vari-able is constant across levels of the othervariable), and c) the rate conditional onboth predictors is exactly the same in everyregion, then ecologic bias due to the covari-ates can be removed or largely reduced byincluding product terms in the linearmodel. Of course, such conditions are verydifficult to verify in ecologic studies; if theexposure and covariates (other risk factors) arecorrelated within regions, the covariates will beconfounders at the individual level and sub-stantial ecologic bias can occur even withproduct terms in the model (81).

When the data are not entirely ecologic(see "Ecologic Designs"), rate standardiza-tion is another method often employed toadjust for extraneous risk factors in ecologicstudies. For example, if the age distributionis known for cases and for the base popula-tion in every region, we can mutually stan-dardize the rate in every region to the agedistribution ofa well-defined (standard) pop-ulation (5); then we use the standardizedrates as the outcome variable in the ecologicanalysis. Unfortunately, this method does

not always reduce ecologic bias due to thevariables for which the rates are standardized;in fact, the result may be to increase biasappreciably (8692). Standardization can beexpected to reduce ecologic bias only if allvariables in the model (i.e., disease and allpredictors) are mutually standardized forthose other confounders (e.g., age) notincluded as predictors in the regressionmodel. This method is often not feasible, forexample, when the investigator does notknow the age distribution of exposed andunexposed populations within every region.

Other Methodologic PrblemsIn addition to ecologic bias and the relateddifficulties of controlling for extraneousrisk factors, there are other methodologicproblems with ecologic analysis, a few ofwhich are addressed below.

Exposure Misclassification Bias. Asnoted in "Sources of Epidemiologic Bias,"nondifferential misclassification of expo-sure status in individual-level studies nearlyalways results in bias toward the null value;e.g., the estimated rate ratio will be doser toone than is the true rate ratio. In multiple-group ecologic studies, however, this princi-ple does not hold when the exposure variableis formed from the aggregated observationsof all individuals in each region (e.g., theproportion exposed). Brenner et al. (93)have shown that nondifferential misdassifi-cation of a binary exposure within groupsusually leads to overestimation of the rateratio (away from the null value) in ecologicstudies, which can be severe. This apparentcontradiction between ecologic and individual-level studies can be understood by consideringjust two regions. Nondifferential exposuremisdassiflcation in both regions will producean estimated difference in exposure preva-lence that is smaller than the true difference.Consequently, the estimated regressioncoefficient (slope) for the exposure variablein a linear ecologic model will be overesti-mated, leading to overestimation of the rateratio. Ltde is known about the impact in eco-logic studies ofwithin-group error in measuringcontinuous or multiple-category exposures.

Confounder Misclasifiation. In stud-ies conducted at the individual level, mis-dasificaion ofa confounder, ifnondifferentialwith respect to exposure and disease, willusually reduce our ability to control for theconfounder in the analysis (94,95). Thatis, adjustment will not completely elimi-nate the bias due to the confounder. Inecologic studies, however, nondifferentialmisclassification of a binary confounderwithin groups does not affect our ability tocontrol for that confounder (96). Thus, sur-


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prisingly, nondifferential milsdassification of aconfounder is less problematic in ecologicstudies, provided there is no ecologic bias, thanin individual-level studies.

Collinearity. It is probably more com-mon in ecologic studies than in other studiesfor two or more predictors to be highly cor-related across groups (63,97,98). This issueis particularly relevant with environmentalfactors, such as the associations between lev-els of different contaminants in air or drink-ing water or associations between differentsocioeconomic indicators. The implicationof such collinearities is that it is very diffi-cult, perhaps impossible, to separate theseeffects statistically; analyses yield modelcoefficients with very large variances andoften severely distorted estimates of effect.

Temporal Ambiguity of Cause andEffect. Use of incidence data in a cohortstudy usually implies that disease occurrencedid not precede exposure to the hypothe-sized risk factor. Yet, in multiple-group ortime-trend ecologic studies use of incidencedata provides no such assurance against thistemporal ambiguity (63). This inferentialproblem is most troublesome when it is pos-sible for disease to influence exposure statuseither at the individual level (see "CohortStudy") or at the ecologic level (e.g., inter-ventions designed to reduce exposure levelsin areas with high rates of disease).

The problem of temporal ambiguity inecologic studies is further complicated byan unknown or variable latent periodbetween exposure and disease occurrence.The investigator can only attempt to dealwith this problem by establishing a specificlag period between observations of averageexposure and disease rate. Even when theaverage latency is known, however, appro-priate data may not be available to accom-modate the desired lag.

Migration. Migration of individualsinto or out of the base population can causeselection bias in any type of epidemiologicstudy, because migrants and nonmigrantsmay differ on both exposure prevalence anddisease risk. Little is known about the mag-nitude of this bias or how it can be reducedin ecologic studies, especially when studyingdiseases with long latent periods. Oneapproach might be to use larger geographicgroups (e.g., states instead of counties asunits of analysis) (99). Unfortunately, thisapproach is also likely to increase the poten-tial for severe ecologic bias, because itmakes the groups less homogeneous withrespect to exposure (see "Ecologic Bias").Another approach might be to incorporateavailable data on the distributions of resi-dential durations within regions, but this

approach needs more work to provide areliable method of bias reduction.

Current Issues andRecommendationsA general goal of epidemiologic research isto obtain the most information about pos-sible health effects with minimal and/oravailable resources. Given the difficultiesin estimating effects of specific environ-mental exposures in human populations, thisgoal is not easily obtained and optimal researchstrategies are not readily identified. Below, wehiglight severl current methodologic issuesin environmental epidemiology and makesome recommendations for future work.

Study Design. No single design bestmeets the objectives of every epidemiologicstudy. In practice, study objectives areshaped by many factors-current knowl-edge, previous findings, institutional man-dates, societal values, personal preferences,etc. Although a prospective cohort studymight be expected, in general, to produceless bias than would a hospital-based (pro-portional) case-control study, the latterdesign might be a rational choice in certainsituations. Even an ecologic design, despiteits limitations, might be appropriate; it maybe the only practical option at a given time.

The challenges of environmental epi-demiology, therefore, cannot be solvedsimply by advocating the use of certain,more expensive study designs. In additionto committing more resources to the con-duct of epidemiologic research, we need todevelop new designs to meet specific objec-tives more efficiently. For example, in"Case-Control Study," we discussed theuse of two-stage designs to investigate asso-ciations between rare diseases and rareexposures and to control for covariates thatare relatively expensive to measure. Newapproaches are also needed to identifyintermediate variables in observationaldesigns, to evaluate interaction effects(effect modification) more efficiently, andto deal with the problems of nonparticipa-tion, nonresponse, and noncompliance.Another need in environmental epidemiol-ogy is to understand better the relationshipbetween acute biological changes andchronic health effects. For example, wemight combine experimental and observa-tional methods to determine the extent towhich short-term changes in pulmonaryfunction caused by exposure to air pollutantslead to chronic respiratory disease (2).

Bias Reduction. In nonrandomizedstudies, it is important for the investigatorto deal with confounding in the analysis.This is achieved by identifying potential

confounders in the design phase and mea-suring them accurately in the study popula-tion. The prevention of selection bias,however, is not so straightforward becauseit depends on identifying all cases thatoccur in a well-defined (base) population atrisk. When new cases occur infrequentlyor when it is otherwise impractical to re-examine enough individuals to detect allnew events, the prevention of selection biasdepends on population surveillance and moni-toring systems, such as population-basedtumor registries and industrial surveillance.Although these systems may be expensiveto implement and operate, they are oftennecessary to reduce the threat ofselection bias.

Unfortunately, population-based sys-tems may not be sufficient to prevent selec-tion bias with diseases for which detectiondepends critically on care seeking, symp-tom reporting, and complex differentialdiagnoses. A key problem is that not allpersons with an illness recognize theirsymptoms and seek medical attention.Thus, exposure effects observed for these dis-eases in epidemiologic studies might reflect theeffects of the exposure on illness behavior aswell as the effects on illness occurrence (100).

Another solution to incomplete orinadequate case detection is to control ana-lytically for methodologic covariates thatreflect differences in illness behavior. Forexample, we might measure the individ-ual's tendency to seek medical care andtreat this variable as a confounder. Themeasurement of this covariate should beindependent of disease status; otherwise,covariate adjustment will probably lead tobias toward the null value. This approachneeds further development and evaluation.

An alternative strategy for studying dis-eases that are difficult to detect in large pop-ulations, such as musculoskeletal conditions,is another type of two-stage design. In thefirst stage, a large population is surveyedcross-sectionally or longitudinally by ques-tionnaires or interviews to identify personswith symptoms characteristic of the disease.The second stage involves case-control sam-pling of the population to compare personswith and without these symptoms (i.e., casesand controls). In this stage, subjects aregiven more definitive diagnostic tests toidentify true cases of the disease. By com-paring diagnostic test results betweenselected cases and controls, the investigatorscan assess the validity of their symptom-based criteria, suggest improvements in din-ical diagnosis, and estimate exposure effects.The latter objective requires the develop-ment of statistical methods appropriate forthe sampling strategy.


35


Quality ofMeasurement. As noted ear-lier (see "Problems in EnvironmentalEpidemiology"), a major challenge in environ-mental epidemiology is to measure accuratelyeach individual's exposure to suspected andknown risk factors for the disease understudy. In the absence of previously validatedand inexpensive methods for measuring expo-sures and covariates in large groups, it hasbecome common practice to use more thanone method or source of information to mea-sure these variables. Nevertheless, it usually isnot dear how different methods or sources ofinformation should be combined or what datashould be combined to minimize measure-ment errors and estimation bias (4,101,102).We need more methodologic research in thisarea to provide guidelines for the measure-ment of specific exposures in particular typesof populations. One approach that might bepursued with environmental exposures is tocombine ecologic data with self-reported dataon individual behaviors. For example, sup-pose we collect ecologic data on pesticidespraying and distribution throughout a largeregion. We could then obtain from subjectsthe location of their homes; the type and loca-tion of their work; their use ofdfinking water;and how often they swim, fish, and partici-pate in other activities that would affecttheir exposure to pesticides in the region.

Frequently, an accurate method doesexist for measuring an exposure, but theapplication of this method to all subjects in apopulation is prohibitively expensive orinfeasible. In such cases, many investigatorsrely on less accurate methods for the totalsample and use the more accurate method ina subsample of subjects. Assuming the accu-rate method is perfectly valid (i.e., the goldstandard), the results of the validation sub-study are used to quantify the amount ofmeasurement error, which is then used in thetotal sample to correct for misdassificationbias involving the imperfect measure ofexposure. Some important issues need to beconsidered to make this approach advanta-geous. First, how many subjects and whatproportion of the total sample should beincluded in the substudy (103,104)?Second, how should we correct for exposuremisclassification in the analysis, especiallywhen the accurate method may not be per-fectly valid or when the subsample is not rep-resentative of the total sample (see alsoPrentice and Thomas, this issue)?

Ecologic Inference. Because of inherentproblems of measurement, most epidemio-logic studies of environmental exposuresare at least partly ecologic. When all data,except a single exposure, are obtained atthe individual level, however, the ecologic

problem amounts to possible misclassifica-tion bias, which is well understood andoften predictable. Yet, when the unit ofanalysis is the group, the resulting ecologicbias is far less predictable and can be rela-tively severe in magnitude, especially whenother sources of bias are present. Thus, ingeneral, ecologic analyses do not providevery accurate estimates of effect. To makeecologic findings more informative, there-fore, we need more theoretical work tospecify the conditions for which ecologicestimates can be expected to be reasonablyvalid. With this information, we mightthen collect additional data to check thosekey assumptions or to correct ecologic esti-mates. For example, by obtaining detailedindividual-level data on the exposure andcertain covariates in samples of selectedgroups, we might be able to determine thelimits of ecologic bias in estimating theexposure effect (see "Control for Covariates"and Prentice and Thomas, this issue).

Essentially, ecologic bias (aside fromwithin-group bias) occurs because group affili-ation or the average exposure level of thegroup affects disease occurrence indepen-dently of exposure status at the individuallevel (see "Ecological Bias"). The structuraleffects ofsuch ecologic variables, ifthey can beseparated from other effects at the individuallevel, might be informative, rather than just asource of error. Thus, by induding both eco-logic and individual-level predictors (possiblyof the same exposure) in the analysis, wemight enhance our understanding of diseaseoccurrence. This type of contextual or multi-level analysis has been used extensively insocial science research (105-108) but rarely inepidemiologic research (109). In addition, ifthe effect of a risk factor is known from previ-ous research, the results of an ecologic analysisinvolving that risk factor could be used toevaluate the potential or realized impact of apopulation intervention, which may not becompletely estimable at the individual level(63). A more profound understanding ofecologic bias, therefore, could yield benefits toother public-health research.

Gene-Environment Interactions. Becauseboth genetic and environmental factors con-tribute to the etiology of most diseases, wewould typically expect factors of each type toconfound and/or modify the effect of theother. We know, for example, that a combi-nation of both environmental/personal factorsand genetic susceptibilities are sufficient forthe development of certain diseases. Yet stan-dard methods of epidemiologic research andpopulation genetics have not been well inte-grated (110). As indicated in "EcologicalBias," we need new methods for incorporating

environmental variables in genetic (e.g., link-age) analyses of pedigree data. We also needto understand better the relationship betweenthose parameters estimated in pedigree studiesand the effect parameters estimated in stan-dard epidemiologic studies; and we need tounderstand better how the estimates ofgene-environment interactions in pedigreestudies are biased by confounding, measure-ment error, and family selection (ascertain-ment). With this understanding, we candevise new methods to prevent or controlbias. Analogously, the use of family data instandard epidemiologic designs (e.g., historyof disease and/or its risk factors in relatives)requires further development in order to han-die differences in family size and compositionamong subjects. With the recent advances inmolecular genetics, the integration of epi-demiology and population genetics is likely tobecome more important in the future.

Sample Size and Power. As noted in"Problems in Environmental Epidemiology,"epidemiologic studies of environmentalexposures often require large sample sizes todetect risk-factor effects with sufficientlysmall statistical error. To address this con-cern, researchers are usually expected to jus-tify their proposed sample size by estimatingthe power of their study for testing one ormore major hypotheses (i.e., the probabilityof detecting an association of at least a cer-tain magnitude with a designated Type Ierror-alpha level typically set at 5%). Thisis a rather straightforward procedure whenthe power estimation is applied to twodichotomous variables (exposure and disease)(1,4,111). Yet all observational studiesrequire more complicated analyses to makecausal inferences- e.g., to deal with polyto-mous, continuous, or time-dependent expo-sures; covariate adjustment; the assessment ofinteraction effects; matching; and other spe-cial design features. Although methods ofpower estimation do exist for many of thesecomplicating features, they require additionalspecifications (assumptions) about which theinvestigator is not likely to have adequateinformation. Further development of thesemethods would be useful, therefore, to iden-tify techniques that are both practical andinformative in specific situations, includingecologic studies for which sample sizerequirements have received little attention.

One parameter the investigator mustspecify to justify the proposed sample sizeis the magnitude of effect expected in thedata or the minimum effect regarded asimportant to detect. In the absence of pre-vious epidemiologic studies involving simi-lar exposure levels, the expected effect isgenerally specified rather arbitrarily (e.g., a


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rate ratio of 2). Sometimes, however, thereare exposure-response findings from ani-mal studies or occupational studies withhigher exposure levels, which could be usedto estimate the environmental exposureeffect expected in the base population.This approach, which also requires furtherdevelopment, might allow research fundsto be allocated more judiciously.

Data Analysis. Many of the recentdevelopments and ideas for new studydesigns and data collection that were dis-cussed in this article require parallel develop-ments in statistical methods. For example,the analyst might have to deal with complexsampling strategies (as in two-stage designs);missing, misclassified, and/or aggregateddata on relevant variables; time-dependent

covariates; lag periods between first expo-sure and disease detection; incomplete casedetection; and a limited sample size thatseverely restricts the number of covariatestreated simultaneously. Several of theseissues are covered further by Hatch andThomas and by Prentice and Thomas inthis issue. eX

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