This manuscript was prepared as part of the Environ-mental
Epidemiology Planning Project of the Health Effects Institute, September
1990 - September 1992.
Epidemiology can be thought of as the study of the variation in disease
occurrence and of the reasons for that variation. Operationally, it involves
making observations in individuals or groups of individuals on the rates
of disease associated with different levels of an exposure or characteristic,
followed by inferences concerning the basis for any differences in rates
seen. At its simplest, epidemiology can involve nothing more than seeking
to correlate published rates of illness in various population groups with
levels of present or past exposure in such groups. However, it generally
is true that stronger inferences can be based on studies of the occurrence
of illness in exposed and nonexposed individuals. Such studies occasionally
involve randomization of individuals to differing environmental exposures
to determine if the subsequent rate of illness (or marker of illness) differs
among exposure groups. More commonly, no randomization is done, but investigators
simply observe rates of illness in persons who happen to have differing
levels of exposure (cohort studies). Also, especially for health outcomes
that are uncommon, it is possible to identify persons with and without a
disease and attempt to retrospectively resurrect exposures that persons
in each group had sustained (case-control studies).
For an epidemiologic study to provide useful information regarding causes
of the disease, several circumstances need to be met. These circumstances
are discussed below:
A. Among individuals otherwise at similar risk of the disease,
there exists substantial variation in the frequency or level of exposure.
From an epidemiologist's point of view, this circumstance is best
met when the variation occurs within members of a community (e.g., the presence
of both cigarette smokers and nonsmokers in a given population). However,
when dealing with certain exposures (e.g., outdoor pollution from acid aerosols
and oxidants or from arsenic), the exposure may be communitywide, with little
variation among individuals within that community. In this situation, it
becomes particularly necessary to make comparisons among populations of
differing exposure status (e.g., air pollution levels) rather than among
individuals within the same population. In many instances, comparisons among
populations are facilitated by the fact that routine data are available
for a variety of health outcomes (e.g., mortality, cancer incidence) on
a large number of populations over a long period of time. Nonetheless, studies
that compare populations rarely can be used for anything but the generation
of hypotheses regarding disease etiology, because a substantial degree of
movement of individuals between communities occurs in most parts of the
world in which these studies are likely to be conducted. This would generally
be expected to dilute any true association between communitywide exposures
and disease occurrence. Also, other bases for a difference in rates among
populations are often quite hard to measure and therefore cannot be taken
into account when looking at the exposure of interest.
For these reasons, some investigators have attempted to study communitywide
exposures on health outcomes by returning to the study of individual persons
within a community, exploiting the substantial degree of migration that
would have occurred in years past. For example, in a study of cancer in
relation to ingestion of asbestos in drinking water, Polissar et al. (1)
compared persons with and without cancer who resided in one western Washington
county. These cases and controls were contrasted with respect to the amount
of time they had lived in those particular areas of western Washington in
which there had been an extraordinarily high concentration of asbestos in
the water supply. Clearly, this approach can be successful only if the induction
period of the disease from the exposure in question is reasonably long.
For residential exposures that truly do vary within a community, this
tendency of persons to change households frequently will act to minimize
variation among individuals in that community. For example, Lubin et al.
(2) note that among Americans in the 1980s there had been a change
of household on the average of every 5 years. If one were attempting to
study cancer in relation to household radon exposure, for example, movement
between households of differing radon levels would tend to neutralize the
more extreme differences that might be present if individuals had resided
in a single household for a longer period of time.
Occasionally, there will not only be interindividual quantitative differences
in exposure (e.g., levels of intensity or duration of exposure) but qualitative
differences as well. Studies of individuals (or groups of individuals) who
vary with regard to type of exposure can suggest what aspect of exposure
might be important in disease etiology. For example, the observation that
occupational exposure to amphibole, more than chrysotile, asbestos is associated
with a particularly high risk of mesothelioma and lung cancer (3)
has a) provided hypotheses regarding the pathogenesis of asbestos
carcinogenicity and b) served, in some countries, as the basis for
different standards for permissible workplace air levels of amphibole versus
chrysotile asbestos.
B. Whether of individuals or communities, the number of units being
compared need be large enough to reliably identify an adverse health effect
of the exposure if one is present. If one or more indoor air pollutants
have a substantial relative impact on the occurrence of a disease, it generally
is possible to identify this in a study of but modest size. For example,
once mesothelioma was identified as such, a study of only a small number
of individuals with and without this condition was needed to determine that
inhalation of asbestos fibers was associated strongly with its occurrence.
However, for many indoor air pollutants, there are reasons to believe that
the true impact on disease occurrence, if any, would be small in magnitude
given the relatively low levels of exposure to these pollutants and the
limited variation in exposure to them in members of the population. The
detection of small relative increases in disease incidence can require a
study that includes a very large number of subjects, even if exposure status
can be measured accurately and possible confounding factors can be taken
into account. Some strategies for achieving a large number of subjects have
included combining in a single study exposed groups that are scattered over
a wide geographic range. For example, in attempting to evaluate the influence
of occupational inhalation of formaldehyde on the occurrence of lung and
other forms of cancer, individuals exposed to formaldehyde in a number of
different work settings and industrial processes in a variety of locations
in the United States were enrolled in a collaborative study (4).
By means of meta-analysis (5), one can formally aggregate the results
of multiple studies that pertain to the health impact of a particular exposure.
C. The health outcome can be assessed with accuracy and in an unbiased
way. Obviously, the inability to recognize distinctive pathologic
process as such will impair our ability to recognize the determinants of
that process. It was not until the last half of this century that mesothelioma
was identified regularly as being present in patients who truly had this
malignancy. Had mesothelioma been routinely diagnosed in earlier years,
undoubtedly our understanding of the carcinogenic potential of asbestos
fiber inhalation would have been achieved earlier as well.
Inaccurate assessment of health outcomes also can give rise to false
positive associations with respiratory exposures. This is particularly true
when the outcome is defined solely on the basis of symptoms. When knowledge
of a person's exposure status could influence his or her reporting of these
symptoms, great care has to be taken to standardize assessment between exposed
and unexposed subjects. Occasionally, it will be necessary to focus the
analysis on the occurrence of symptoms of great severity. For example, in
their study of possible neurologic sequelae of swine flu vaccination, Marks
and Halpin (6) labeled only patients with bilateral lower motor neuron
weakness of acute onset as having Guillain-Barré syndrome. They feared
that, because of the concern that many patients and their physicians had
regarding this vaccine, less specific neurologic illnesses would be identified
more completely in vaccinated than in unvaccinated persons.
D. Exposure levels can be (or have been) measured accurately and
at the appropriate time relative to the induction period of the disease
under study. In many studies, whether cohort or case-control in
type, the cases of disease have occurred already by the time of the study.
Exposures that have occurred earlier in time need to be assessed. One way
of doing this is to ask subjects, both those with and without disease, about
their prior exposures. An advantage of this approach is that information
can be sought about several different time periods. The primary disadvantage
of the approach, however, is the relative imprecision with which the information
generally can be provided. While persons might know they have been exposed
to some extent to environmental tobacco smoke, for example, they would find
it difficult to quantify this exposure in an accurate way. For other types
of exposure (e.g., radon), no subjective assessment is possible. Direct
measurements of present exposures can be made, but responsibility falls
on the investigator to take steps to assess their comparability to exposures
that the subject sustained in the past. For some (e.g., residential radon),
this is more feasible than for others, because prior radon exposures can
be estimated from present ones given the known decay of this element combined
with additional information on structural and other alterations to the residence.
At first glance, it would seem that studies in which measurements are
made at the time the study begins, with subsequent monitoring of the occurrence
of illness, would have substantial advantages over those that try to ascertain
exposures in a retrospective way. However, there are at least two important
limitations of these prospective studies: a) Unless the follow-up
period is very long, the study population very large, or the disease under
study very common, the number of health outcomes that occur may be small
and may yield highly tentative results. b) Depending on the length
of the induction period for the disease, single measurements made at the
start of the study may not be relevant for long to disease occurrence. For
example, in their prospective study of environmental tobacco smoke in relation
to the occurrence of fatal coronary heart disease, Garland et al. (7)
assessed exposure to spouse's smoking via an interview. Among members of
this cohort, the occurrence of fatal heart disease was then monitored during
the next decade but with no additional information regarding continued exposure
to spouse's smoking. If exposure to environmental tobacco smoke predisposes
to the occurrence of fatal heart disease through a relatively short-term
mechanism (perhaps via acute toxicity of elevated levels of carboxyhemoglobin),
this research approach would be a relatively insensitive means of addressing
the hypothesis, given the occurrence of changes in the exposure to spouse's
smoking during the extended follow-up.
E. An unbiased sample of exposed and nonexposed individuals has
been selected for study. While this is a concern in any study, it
is a particular problem for those that are cross-sectional in nature. In
such a study, exposed and nonexposed individuals are contrasted for their
prevalence of disease. A seriously biased underestimate of the health impact
of the exposure will be obtained if persons who have suffered disease because
of the exposure are no longer present at the time of sampling (e.g., through
premature retirement from a hazardous occupation or due to death). For example,
in the 1940s, Fleischer et al. (8) noted only a low prevalence of
asbestosis among men who had been employed as pipe coverers in a shipyard
and who, through this employment, had been exposed to asbestos. Undoubtedly,
the selective removal from employment of those who already had been affected
by asbestos led to the overly optimistic conclusion by the authors that
there was little to be feared in terms of levels of asbestos exposure present
in that occupation at that time.
F. Other factors besides the exposure in question that relate to
the occurrence of disease have been (or can be) measured as well. Measurement
of such factors will enable, first, the control of potential confounding
effects of these other variables (and thus the prevention of the distortion
of the true association between the exposure and disease). For example,
in a study of respiratory infection during childhood in relation to exposure
to environmental tobacco smoke and nitrogen dioxide, it would be important
to ascertain such things as exposure to infected individuals, household
crowding, etc. Second, the characterization of other exposures can enhance
the power of the analysis by allowing an examination of the effect of the
exposure in question according to the presence or absence (or level of)
other risk factors for disease. If, for example, domestic exposure to radon
were a cause of lung cancer only in the presence of active cigarette smoking,
an analysis that failed to examine the association separately in cigarette
smokers and nonsmokers would provide a blurred result. On the other hand,
if domestic radon exposure and cigarette smoking acted via separate causal
pathways to produce the disease (as appears at least in part to be the case
for occupational radon exposure and cigarette smoking) (9,10),
then the relative impact of exposure to domestic radon would be far more
discernible in nonsmokers with their low background rate of lung cancer
than among cigarette smokers in whom there is a high background rate (11).
Conclusions
The foregoing has indicated some of the major threats to the sensitivity
and validity of epidemiologic studies of the health consequences of indoor
air pollution. While these threats are real, it would not be prudent to
allow their specter to paralyze prospective investigators and discourage
them from performing research in this area. Not all of the above criteria
need be met in order for a study to produce some useful information. For
example, the hypothesis that military service during the Vietnam war era
predisposed people to the subsequent occurrence of suicide received strong
support from a study (12) that found an increased rate of suicide
among men whose birthdates made them eligible to be drafted during that
time. Despite the great imprecision with which actual military service in
Vietnam was assessed (it is estimated that only 25% of individuals with
draft eligible birthdates even entered the armed forces) and the modest
size of the association (the study observed a relative risk of 1.13), the
randomized nature of the investigation and its ability to neutralize the
effect of potential confounding variables made for convincing results.
Imprecise exposure assessment also was a problem in a cancer registry-based
study of the hypothesis that homosexual men are at increased risk for the
occurrence of anal cancer (13). Registry data do not provide information
on sexual preference, but they do contain data regarding marital status.
The investigators found that the percentage of men with anal cancer who
had never been married was more than three times that of demographically
comparable men with colon or rectal cancer. Of course, being a single male
is hardly an accurate predictor of homosexual preference. Nonetheless, given
the exceedingly strong association between a history of anal intercourse
and anal cancer (found subsequently in response to the registry-based study),
even a study that measured exposure status as imprecisely as this study
was able to make a contribution.
The important findings in these last two studies, studies that had serious
flaws as measured by the criteria that have been put forth here, should
serve to dispel the notion that only perfect studies will permit progress
toward understanding the harmful effects of indoor air pollution on health.
Imperfect studies, properly interpreted, are far better than none at all.
