Chemistry Reference
In-Depth Information
The study can either focus on cases with the effect as
compared with a control group without the effect, or it
can focus on persons with the metal exposure and com-
pare them with people without exposure. The fi rst type
of study is called a case-control study (Table 1). The cases
and non-cases are compared concerning their metal
exposures in the past or the present based on analysis
of indicator tissues. Higher doses in the group of cases
may be interpreted as an association between the metal
and the effect.
Absolute
occurrence and dose-response
relationships cannot be measured using a case-control
study alone, but a
relative
occurrence between groups
with different dose levels can be calculated in the form
of an
odds ratio
. If both the cases and the controls are
stratifi ed into groups according to metal dose, the odds
ratio for each stratum can be calculated; this ratio can
be expressed as a dose-response relationship. Case-
control studies are often retrospective, because the
analysis starts out from the people with effects, and
their relevant metal exposure for these effects must
have occurred in the past. The term retrospective study
has, therefore, often been used in the past as a syno-
nym (Beaglehole
et al.
, 2000). It should be pointed out
that retrospective data collection might increase errors
in exposure estimations, because of the inherent dif-
fi culties in “reconstructing the past.”
To measure the
absolute
incidence or prevalence
rates needed to establish complete dose-effect or
dose-response relationships in different dose groups,
a cohort study (follow-up study) would be the most
suitable. In this type of study, an exposed group and a
nonexposed group (controls) are selected. The occur-
rence of effects of the metal is measured in each group.
The exposed group can be stratifi ed into groups
according to dose level. The measurement of incidence
or prevalence of effects in each group forms the basis
for dose-effect and dose-response relationships.
One of the most important steps in an epidemiologi-
cal study is the selection of the groups under study.
In both descriptive and analytical (follow-up) studies,
it should be ascertained that the people in the exposed
group are really exposed and belong to the population
at risk. Ideally, the entire group that is and has been
exposed should be studied, or if the group is too large,
a randomly selected sample from this group should
be studied. In an industrial environment, this means
that all workers who were ever exposed in the fac-
tory under study should be included. An operational
defi nition for “exposed” may be used such that an
exposure duration limit is set (e.g., having worked in a
metal-exposed area of a factory for 1 year or longer). If
only workers actively working at the time of the study
are included, those with the effect may be selectively
excluded, because they had to stop working when
they contracted the effect. In a dose-response study
of cadmium-induced tubular proteinuria (Kjellstrom,
1977), it was shown that the possible underestima-
tion of response because of selective exclusion might
be considerable. A similar bias may occur in stud-
ies based on population screenings where only those
healthy enough to come to the screening can partici-
pate. Selection bias may also be introduced in studies
of industrial workers by the procedure of preemploy-
ment selection of workers. Mainly healthy young men
would be selected for the work that involves metal
exposure, and the results of such a study may not be
applicable to the general population. This is called the
healthy worker effect
and is a problem in, for example,
retrospective follow-up studies of mortality (Kitagawa
and Hansen, 1973; McMichael, 1976).
The selection of the control group in analytical follow-
up studies is as important as the selection of the exposed
group. Selection bias caused by, for example, sick people
who are not able to participate, should be avoided. If any
sampling of the exposed group takes place, the same cri-
teria for sampling should be used for the control group.
In case-control studies, similar problems of selec-
tion occur as in follow-up studies. A clear defi nition
of “a case” is needed, and often this has to be based
on an operational defi nition from symptoms, signs,
and biochemical or physiological measurements. The
selection of a “control” in a case-control study is some-
times a problem, because it is necessary to fi nd cases
and controls in the same source population, the study
base (Rothman and Greenland, 1998) (which may be
restricted by age, gender, etc.). For example, if cancer is
the effect studied, ideally the wider population in which
the cancer cases occur should be the source of the con-
trols. In some studies of hospitalized cancer cases, other
hospital patients without cancer have been selected as
controls. These controls naturally have some other dis-
ease, because they are also hospital patients, and if this
disease is also associated with the metal exposure, the
epidemiological analysis may be invalid. In the choice
between follow-up and case-control at the design stage
of the study, it should also be pointed out that the size of
the study group needed for a particular statistical power
in the conclusions depends on whether the exposure or
the effect is rare. If the exposure is rare, but the exposed
people can be identifi ed, a follow-up study needs a
smaller group than a case-control study. If the effect is
rare, the opposite is true. If both exposure and effect are
relatively common (e.g., in more than 10% of groups
studied), either type of study can effectively be used.
Confounding factors can interfere with epidemio-
logical analyses. A confounding factor is something
that is associated with both metal exposure and the
effect; for example, heavy drinking is associated with
