Environmental-Epidemiology Studies: Their Design and Conduct
This chapter discusses the origins of epidemiologic study and summarizes common analytic techniques. After a brief discussion of study designs and the types of information they produce, this chapter notes several difficulties for studies of environmental epidemiology, including the problems of studying small numbers of persons or rare diseases. We recommend that research on study designs focus on the improvement of statistical power or probability of detecting an effect. Finally, we review principles for inferring causation in epidemiology.
Origins of Epidemiology
Although early epidemiologic studies often focused on infectious diseases and death, epidemiology today has a much broader application, as ''the study of the distribution and determinants of health-related states and events in specified populations and the application of this study to the control of health problems" (Tyler and Last, 1991, p. 12). Traditionally, epidemiology has been linked with disease prevention, in that its results can indicate risk factors that can be modified in order to control or eliminate certain diseases.
As chapter 1 indicates, environmental epidemiology is a logical extension of the field, expanding the range of concerns to include biologic, physical, or chemical factors that may be related to patterns of health and disease in populations. In general, environmental epidemiology is an observational rather than an experimental science; scientific deductions are drawn from patterns of occurrence. Its principal aim is to identify risk
factors that can be averted or reduced so as to prevent or reduce the risk of future disease and promote public health.
Types of Studies in Environmental Epidemiology
Environmental-epidemiologic studies can be classified broadly into 2 categories that are not mutually exclusive: descriptive and analytic. Typically, descriptive studies are most useful for generating hypotheses and analytic studies most useful for testing hypotheses, though each type of study can be used for both purposes. Whether a study is hypothesis-testing or hypothesis-generating depends more on the sequence of past studies and the present state of knowledge (i.e., whether a hypothesis currently under evaluation was suggested by a previous study) than on the study design. Recent innovations in descriptive studies sometimes permit refined assessments of dose-response relations and etiologic factors.
Descriptive studies include case reports, surveillance systems, ecologic studies, and cluster studies (WHO, 1983).
A case report is a descriptive study of a single individual or small group in which the study of an association between an observed effect and a specific environmental exposure is based on detailed clinical evaluations and histories of the individual(s). These reports require few financial or personnel resources other than those of clinical medicine, and they may indicate whether additional study of a larger group of persons with similar health problems and exposures should be undertaken. However, the value of case reports is often limited because they lack a context of the disease in unexposed persons, variables such as time and dose of exposure are generally not known, and controls are absent. They are most likely to be useful when the disease is uncommon and when it is caused exclusively or almost exclusively by a single kind of exposure. In spite of these limitations, many known human environmental toxicants (e.g., methyl mercury, asbestos, tobacco smoke, and radon) first came to attention in case reports and series developed by astute clinicians, pathologists, and health workers. Public-health agencies must often investigate clusters of cases that are reported to them by private physicians and others. While case reports may not lead to identification of new causes of disease, they are more likely to point to specific hypotheses and to biologically meaningful associations if either the disease or the exposure is relatively rare.
These systems provide broad-scale information on specified populations for which epidemiologic analyses can be conducted. Surveillance systems are generally designed to attain complete or nearly complete coverage of every identified instance of certain defined conditions in a defined population. Thus, they can be used to estimate the background incidence and prevalence of adverse effects, and trends can be analyzed across time and between populations or geographic areas.
Surveillance systems can identify increases or decreases in the occurrence of deaths from specific diseases and thus suggest or test hypotheses related to environmental exposures. For example, observations of a decline in age-adjusted stomach-cancer rates over time in the United States have stimulated the development of hypotheses about changes in dietary habits in the population as a whole, as well as about changes in the use of food preservatives and refrigeration (Howson et al., 1986) that might explain these trends. Similarly, after postmenopausal estrogen use fell in the United States, rates of endometrial carcinoma declined in women over age 65, lending support to an inference drawn from case-control studies that postmenopausal estrogen use increased the risk of endometrial cancer (Austin and Roe, 1982). In another instance, surveillance data from the National Center for Health Statistics suggested that a fall in blood-lead levels in US children was linked to a drop in gasoline-lead levels (Annest et al., 1983).
As public-health agencies have expanded the scope of surveillance systems (see chapter 5), it has become feasible to study the relationships between disease patterns and variations in environmental factors. Surveillance systems are expected to become increasingly common because the quality of their data is rising, statistical methods are improving, and costs are declining. The Agency for Toxic Substances and Disease Registry (ATSDR) has devised several surveillance systems to monitor the health of persons believed to have incurred exposure to such substances as trichloroethylene and dioxin. No results are yet available from those systems. If these exposure registries are to produce valuable results, they will need to include sufficient numbers of persons over a long enough period for diseases of interest to manifest themselves in numbers sufficient to demonstrate that some problem exists or that the problem is unlikely to exist and be large enough to cause serious concern.
Ecologic studies explore the statistical connection between disease and estimated exposures in population groups rather than individuals. They combine data from vital records, hospital discharges, or disease registries
with grouped data or estimates of exposure, such as factory emissions in a given geographic area, proximity to waste sites, or air or water pollution levels. Observed associations may provide support for further investigations. Ecologic studies suffer from serious weaknesses: they assign group exposure levels to all members of the group, fail to control for individual confounding factors, use necessarily crude estimates of exposure, and may not capture the relevant exposure at the time of disease induction. Although some population groups in ecologic studies may appear similar to "cohorts" (see below), they lack the individual data that permit their analysis in a cohort study. The "ecologic fallacy" refers to drawing inferences incorrectly from data on groups or about individuals in the groups.
Several advances have facilitated an increase in the number of ecologic studies, including the development of surveillance systems, improved environmental-exposure databases (e.g., by ASTDR), and increased availability of sophisticated tools, such as geographic information systems. The value of ecologic studies may be strengthened as methods for estimating exposure are improved. Where valid proxies for gradations of exposure and relevant confounding variables can be devised, the ecologic fallacy may be reduced or overcome.
Ecologic investigations have provided important clues about causal associations even though these studies can be difficult to interpret. For example, fluoride was first found to prevent dental caries on the basis of observed correlations between geographic variations in natural levels of fluoride and rates of tooth decay (Dean et al., 1942). Similarly, rates of cardiovascular disease and cancer among immigrants have been correlated with those of their newly acquired compatriots, suggesting that changes in dietary and other factors are involved. Further refinements in the parameters of interest in ecologic studies might permit these studies to generate more-precise indications of associations between risk factors and disease (Greenland, 1990).
Studies of health problems in relation to fixed sources of environmental exposure have often relied on either labor-intensive techniques, such as personal interviews, or much more general classifications, such as ZIP code or town of residence. The latter approach has the obvious problems of errors in classification of actual residence and of including people in the exposed category who live far from the site and have little opportunity for exposure. This difficulty has been partially overcome by including better geographic-location information as part of state and federal lists of potential sources of environmental exposure (e.g., Superfund sites) and by public availability of more-complete coding of geographic information in US census data.
This additional information, along with the availability of improved mapping software, has greatly improved our ability to link health data,
such as cancer incidence with residence near a source of environmental exposure. With good geographic coding, disease cases and controls can be readily and quickly located in relation to an environmental source so that various measures of distance and direction can be studied. Data on the number and characteristics of people living in the area can also be obtained from census data.
A cluster study is a descriptive study of the population in a geographic area, occupational setting, or other small group in which the rate of a specific adverse effect is much higher than expected. Further, the group is often defined after the fact; that is, the "cluster" comes to attention, and the group is then defined so as to include it. Thus, clusters usually have the drawbacks of small samples. Cluster studies suffer from a major tautology: the data that inspire a hypothesized relation between a given exposure and a specific health outcome tend to be used to test this hypothesis, and then exposure and risk-factor data may be generated for persons defined to be in the study group and, usually, in some control group. For example, a reported cluster of cardiac birth defects that occur near a hazardous-waste site may be "tested" by comparing the measured rates of these defects in the same given geographic area with those from outside the same area. This is a highly unreliable approach methodologically and statistically, as the sample being studied has not been randomly selected. Nonetheless, the approach can be useful when the relative risk is extremely high, and it can be useful in developing hypotheses for study with other data. Many occupational hazards were first identified because clusters of disease were detected in specific workplaces, and other environmental diseases may also be ascertainable through cluster analysis.
In contrast to descriptive studies, analytic studies are based on more individually detailed data from individuals that can be used to control for confounding, and they are usually more costly and labor-intensive. Information from medical records, clinical or laboratory investigations, questionnaire results, or direct measures or estimates of exposures may allow analytic studies to explore hypotheses about suspected causes of disease or identify and measure risk factors that increase the chance that a given disease will occur. Analytic studies may also be a source of additional specific hypotheses, often leading to a sequence of studies, the more recent being designed to attempt to refute hypotheses raised by earlier studies.
The classic designs of analytical studies are case-control and cohort studies. In addition, 2 "hybrid" designs—nested case-control studies and case-cohort studies—can be based on identified cohorts.
Case-control studies compare exposures of individuals who have a specific adverse effect or disease with exposures of controls who do not have the effect or disease; controls generally come from the same population from which the cases were derived. There is an extensive literature on the design of case-control studies, including selection of controls, correction for confounding, statistical methods for analysis, and presentation of measures of effect, usually the odds ratio (Schlesselman, 1982). These studies generally depend on the collection of retrospective data. They may suffer from recall bias, i.e., the tendency of people who have a disease to remember putative causes more readily than those without a given disease. However, it is often possible in a case-control study to collect histories of exposure to many different factors and control for confounding more efficiently than in a large cohort study, where the costs of collecting substantial exposure data from all the members of the cohort may be prohibitive. It is likely that case-control studies will be conducted with increasing frequency as new ways of characterizing exposure through the use of biologic markers are developed (see chapter 3), mirroring the development that has occurred in the last 2 decades in other areas of epidemiology.
These studies identify a group of persons called a cohort, or sometimes several cohorts with differing kinds of the exposures of interest. Sometimes, a control group has zero exposure. The cohort study evaluates associations between the exposure(s) and 1 or more health outcomes in the cohort(s). In a cohort study, individuals with differing exposures to a suspected risk factor are identified and then observed for the occurrence of certain health effects over some period, commonly years rather than weeks or months. The occurrence rates of the disease of interest are measured and related to estimated exposure levels.
Cohort studies are of 2 kinds—retrospective and prospective—each with advantages and disadvantages. The retrospective (or historical) cohort study relates a complete set of outcomes already observed in a defined population to exposures that occurred earlier; data on both exposure and outcomes must be available at the time the study is undertaken. Prospective cohort studies, in which current exposure is directly measured
and individuals are then followed, have a potential for more-accurate measurements but may suffer from loss of subjects to followup or bias in ascertainment of end points. Also, it may be necessary to wait for many years or even for the time of followup to exceed the latent period between exposure and effect or for sufficient outcome events to occur.
Cohort studies can utilize questionnaires or laboratory tests to measure both exposure and outcome. One advantage over case-control studies is that multiple outcomes can be evaluated simultaneously in relation to the exposure data. However, the power to test associations will depend on the frequencies of the different outcomes considered, which in turn depend on the number of persons followed (see discussion below on power considerations).
One type of cohort study seeks to correlate time trends in outcome measures and environmental exposures. Such studies can be divided into 3 broad classes: those in which the outcome is estimated or measured relatively few times, those in which outcome variables are linked to episodic variations in exposure, and those in which long-term time trends in measures or estimates of health outcomes are linked with variations in monitored or estimated exposures. The first class is seen in some cardiovascular studies in which determinations of health status are made annually. Outcome measures are often continuous, as well as dichotomous. Other examples are those that correlate the development of chronic bronchitis with exposure to air pollution and prospective cohort studies that follow children's lead exposure and cognitive development from conception or birth. The second broad class examines changes in response to exposures that are episodic or of short duration. Studies that link peaks in air pollution to patterns of asthma fall into this category. The third broad class is similar to time-series studies often conducted in the social sciences. In such studies, both exposure and outcome measures are collected, perhaps on a daily basis, for periods of months or even years. Short-term fluctuations in those outcomes are correlated with short-term variations in environmental exposures. For instance, studies of changes in peak respiratory flow, respiratory symptoms, hospital admission, and daily mortality can be linked to changes in environmental air pollution. In most of these studies, the multifactorial nature of the outcome means that the explanatory power of each environmental variable is generally small. This has necessitated relatively large samples and careful modeling to avoid potential confounding.
Nested Case-control Studies
These studies are similar to ordinary cohort studies except that only a sample of controls (persons free of the disease) are studied in detail. They
generally use old cases in a defined cohort that has been followed long enough for sufficient outcome events to have occurred but only a random sample of cohort members who were eligible to become cases but had not developed the disease or died at the time the corresponding cases were diagnosed. Controls are often matched to cases on 1 or more potential confounders (e.g., age, sex, and smoking status) that the investigator does not wish to study. An individual selected as a control may become a case if the disease of interest develops. Nested case-control studies can be designed to have almost as much statistical power as the cohort study from which they are derived because of tighter experimental control, and they can be used to derive better inferences on exposure-disease associations. These studies may also be substantially more economical if the determination of exposure of the controls can be limited to a sample.
In this design, a random sample of the total cohort is drawn and taken to represent the exposure experience of the cohort. When the cohort has been followed long enough to accrue sufficient cases for analysis, the exposure experience of this subcohort is compared with that of the cases (who arise from the total cohort and might or might not be individuals in the subcohort who become cases). This design also provides economies in obtaining exposure data compared with a cohort study, but surveillance of the total cohort is still needed to identify the cases that occur.
Many epidemiologic studies explore the relation between risk factors and health outcomes, often examining the relation between a single exposure and a single factor or disease. In environmental epidemiology, however, both exposures and outcomes are usually multiple. Many of the risk factors of interest derive from large-scale data sets on environmental pollution that involve continuous variables, as well as a variety of clinical health indicators. Much of cancer epidemiology has focused on studying specific anatomic sites of cancer and delineating important contributors to specific types of cancer, such as the link between occupational exposure to benzene and leukemia or that between asbestos and mesothelioma. Similarly, much of cardiovascular epidemiology has involved prospective cohort studies that concentrate on identifying a few specific risk factors.
Many environmental-epidemiology studies are cross-sectional. In such designs, the relations between contemporaneous assessments of out-
come and exposure are studied; this can give rise to difficulties in determining the temporal aspects of an association. Often the exposure variable is measured continuously but with substantial error. The outcome is generally multifactorial, requiring a large number of covariates, and can include a wide range of health effects for which standard nomenclature, coding, and test systems do not exist. Examples of such outcomes include neurologic outcomes used in studies of lead toxicity, outcomes of some pulmonary-function tests, and diaries of activity level. Environmental epidemiology often relies extensively on a complex of study designs, such as cross-sectional designs that meld both analytic and descriptive studies, and often considers multiple health outcomes as well as multiple exposure variables.
Recent advances in molecular biology provide new ways to identify and measure markers of exposure or outcome, such as DNA adducts or oncogenes, that are identified through molecular biology. Such data can be used in any of the epidemiologic methods, so such studies have been designated "molecular epidemiology" by molecular biologists. The committee addresses the utility of biologic markers of exposure further in chapter 3 and biologic markers of outcome in chapter 4. However, the committee notes that the application of molecular biology to humans as distinct from experimental animals does not in itself justify the term "molecular epidemiology." For a study to be classed as molecular epidemiology, it is essential that valid epidemiologic techniques and study designs be used, including the selection of study subjects from a defined population. This field can develop only if epidemiologists and molecular biologists collaborate in the design and conduct of such studies. In the absence of adequate implementation of both aspects, the term molecular epidemiology should not be used.
Considerations of the Power of Study Designs
Before any study is undertaken, sound epidemiologic practice requires careful consideration of statistical power, that is, the probability that a given research study will be able to detect a true positive effect if it exists. A study's power depends on many factors, including the increases in risk of exposed persons for the outcome under study, the size of the population to be surveyed, and, for cohort studies, the duration of followup. The higher the expected relative risk (RR), the smaller the population that needs to be surveyed. Conversely, the larger the population studied, the smaller the RR that can be detected. Most environmental pollution
includes relatively low levels of exposure to complexes of poorly defined materials. Thus, an environmental pollutant is likely to be associated with relatively small risks, though it could affect large numbers of people.
At any given level of statistical significance, there is a relation among study power, sample size, prevalence of exposure, and expected rate of a given outcome. In general, studies of larger numbers of persons over longer periods are more likely to yield positive results than those involving smaller populations for shorter periods. However, even large studies with long followup will result in uncertain findings if exposure is poorly measured or misclassified (see chapter 3). The sample size needed to achieve a given study power is also related to whether exposure is measured as a dichotomous or continuous variable, to the variability in distribution of the exposure, and to the effects of confounders and errors in the measure of exposure. In general, larger samples are needed when exposure measures are not continuous, when the effects of confounders and errors of measurement cannot be taken into account, and when the adverse outcome is a rare event (Greenland, 1983; McKeown-Eyssen and Thomas, 1985; Lubin et al., 1988; Lubin and Gail, 1990). Finally, all statistical-power calculations depend on the critical assumption that bias in both exposure and outcome can be ignored; this assumption may be rarely true in practice.
Statistical-significance testing is used to assess the likelihood that positive results of any given study represent a "real" association. However, no matter which statistical tests are employed, common research designs all produce studies with fixed, known chances of making a type I error, that is, of finding a positive result when one does not really exist. This probability is called alpha and is generally determined by a statistician at the time the protocol is drafted. It is commonly set at 5%.
Of equal importance for environmental epidemiology is a consideration of the probability that a failure to find an effect is a false negative, or type II error. This often occurs when small numbers of persons are studied and when relatively low risks are involved. Statistical tests cannot determine whether or not an error has been made but can indicate the probability that an error could occur, called beta, if the effect is of some hypothetical size specified by the investigator. The power to detect an effect of that size, defined as 1-beta, depends on the alpha level of significance testing and the unknown relative risk. Tables have been devised to help determine the number of observations required to have specified power to detect an effect of specified size if an association exists (Fleiss, 1981). For any specific size of effect, the power of a study increases as the study size increases.
Many episodes of environmental contamination involve low relative risks and small numbers of people, so environmental-epidemiology stud-
ies often lack sufficient power to detect important effects. This makes the development of innovative techniques to combine results an important priority for the field.
P values are measures of random uncertainty alone and are dominated by sample size and other power considerations. In observational epidemiology, the primary sources of uncertainty about whether an effect is present are confounding, selection bias, and similar problems. In contrast, measures of the size of a possible effect, such as regression coefficients or odds ratios, may be less sensitive to sample size. If associations are due primarily to confounding, investigators may report considerable variation in measures of effect across different studies and populations. Hence, in modern epidemiology these measures of effect, and confidence intervals for them, are given greater attention than P values. Consistency in these measures across studies with differences in exposures to potential confounders can provide valuable clues about whether observed associations indicate cause-effect relationships.
A very severe problem in environmental epidemiology is known as ''multiple comparisons." If the probability of an error with 1 comparison (P value or confidence bounds) is kept at the traditional value of 5%, a research study that includes more than 1 such comparison has a higher chance of making at least 1 error. While statistical methods exist to remove this effect, they have an unintended and often devastating effect on statistical power. This matter is dealt with in many statistical texts, so we do not expand on it here.
Causal Inference in Epidemiology
The previous volume elaborated on criteria relevant to drawing inferences from epidemiologic studies (see NRC, 1991, for general guidance on these studies). They are summarized here as follows.
Strength of Association
The strength of association measures the size of the risk that is correlated with a causal agent (exposure). It is typically expressed as the risk of an exposed person's incurring a disease compared with that of a non-exposed person. The most-common comparison measures are the standard mortality ratio (SMR), the odds ratio (OR), and the relative risk (RR). The larger the ratio (SMR, OR, or RR), the stronger the association between the inferred link of exposure to disease for exposed individuals. For example, an RR of 1.4 for lung cancer after exposure to environmental tobacco smoke indicates that exposed persons are 40% more likely to develop lung cancer than are non-exposed persons. The strength of associa-
tion must often be considered in relation to the population at risk and intensity of the exposure. For example, an RR of 4 that affects a small population may have a much smaller public-health impact than does an RR of 1.2 that affects much larger numbers. Epidemiologists are sometimes concerned with attributable risk, which is a measure of the rate of disease above the background rate that can be attributed to exposure. This is more difficult to detect, study, and estimate in environmental epidemiology because it is difficult to determine a baseline rate. Problems with using strength of association as the principal criterion for causality include the fact that misclassification and other biases can profoundly change the strength of association.
Specificity of Association
Specificity suggests that the suspected causal agent induces a single disease. While this may apply to a few associations between exposure and disease (e.g., vinyl chloride and angiosarcoma of the liver), single diseases (e.g., lung cancer) can have many causes, and single agents can cause many effects (e.g., lead at high-enough levels can cause increased blood pressure, neurologic symptoms, reproductive effects, and kidney damage). Specificity can be diminished by inappropriate or inaccurate grouping of diseases in a way that obscures a real effect (e.g., grouping some rare forms of cancer with other cancers).
Consistency of Association
The observed relation between exposure and disease is seen rather regularly in independently conducted studies; the value of consistency is enhanced if the studies are of different types and in different populations. For example, a study of the association between lung cancer and passive smoking may produce an RR of only 2.0 or less, but this elevated risk has now been reported in over 30 studies carried out in 6 countries (NRC, 1986). Because of the variety in study protocols and populations, claims of bias in all the studies have little credibility. Studies not having statistically significant results can be combined with similar studies, as long as they all use sound methods. Studies that meet the standards for good epidemiologic practice can be grouped for meta-analysis, which allows for statistical pooling of different studies.
The exposure should precede the development of symptoms or diseases of interest by an appropriate interval. The time between exposure
and disease should be consistent with biologic understanding of the time from exposure to the observed disease. For example, tobacco typically causes lung cancer 25 years or more after the beginning of regular exposure, though a few cases have been observed within 10 years of first exposure (Doll and Peto, 1978).
Biologic Gradient of Relation Between Estimated Exposure and Disease
In general, a greater exposure should cause a stronger (though not always proportional) effect. For example, smoking more cigarettes increases the risk of lung cancer. Typically, dose equals the concentration integrated over time. In some cases, however, dosing patterns can be more important than the overall dose in the relation between dose and response. Also, the timing of the exposure can be critical in the dose-response relation.
Effects of Removal of a Suspected Cause
If a causal relation exists, removing the causal agent should reduce or eliminate the effect; if the effect is irreversible in individuals already exposed, this reduction may not be apparent until the exposed generation is largely removed from the study population by death or in some other way (e.g., limitation to persons under age 65). If different causes are related to a single disease, then the principle applies only to the specific causal factor removed.
The relation between the suspected causal agent and suspected effect should make sense, given the current understanding of human biology. Animal studies or other experimental evidence can strengthen or weaken the biologic plausibility of the relation by demonstrating mechanisms of disease or determining whether the association between exposure and disease holds in experimental situations. However, lack of a known mechanism does not invalidate a causal association. For many diseases, the underlying mechanisms are unknown.
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