384 EPIDEMIOLOGY
in association with the presence of the disease, and less so
with its absence.
A case-control investigation led naturally to this end
point, though it may take a variety of different forms. Take
one of the earliest studies of smoking and lung cancer, Doll
and Hill (1950), which was followed by a cohort of English
physicians using a questionnaire (Doll and Hill, 1954) and
then continued as a prospective study up to the present day
(Doll et al., 2004). For this study 709 patients with lung
cancer, in 20 hospitals, were matched with the same number
of patients from the same hospital, but not having cancer or
a respiratory disease. The matching was for the same hospi-
tal, of the same sex, and within the same 5-year age group.
All the patients were interviewed according to a standard
questionnaire. The simplest form of the results is shown in
Figure 11.
The expectations in the two lower cells of the square
are each 40, and in the upper cells each 699. The difference
therefore in each cell is 19, with the result that the X^2 value,
whether or not Yates’s correction is used (it is not necessary
here), is very large, and the probability that the association
between smoking and lung cancer might be a chance one is
extremely unlikely. In the study itself the result of smoking
(in numbers of cigarettes smoked per day) was quantifi ed,
and the results given separately by sex. For the purpose of
this illustration the study is summarized in Figure 11, but
clearly the additional evidence afforded by the quantifi cation
data, which for each sex showed a steadily increasing risk of
lung cancer at each successive level of smoking, reinforces
the basic etiological relationship of smoking to lung cancer.CASE-CONTROL STUDIESIn any case-control study (“case-referent study” is a synony-
mous term) the choice of appropriate controls is of special
importance. In the study discussed above, the controls were
matched for sex and age group—the two most commonly
used characteristics for matching—and also for hospital, lest
there should be some factor associated with that. There were
two exclusions: cancer and a respiratory condition, which
could confuse the contrast between cases and controls. When
there are few cases available, and in some other circum-
stances, it may be advisable to use more than one control per
case. Beyond four controls per case little further advantage
can be gained, but two, three, or four controls for every case
may be useful, though expensive. In general the more closelythe controls resemble the cases in terms of characteristics, the
more effi cient the contrast, except that one or more of those
characteristics may be of genuine etiological signifi cance, but
because it is possessed by both case and control, it is impos-
sible to distinguish.CLINICAL TRIALSThe underlying philosophy is that of the experimentalists of
the scientifi c renaissance, who began in physics or in chem-
istry to look at the effects of a single factor alone, varying
its contribution to the ultimate effect while endeavoring
to keep other factors constant. The method could then be
repeated for other factors, and thus the independent effects
assessed, as well as those where separation proved impos-
sible because of close correlations. The aim of the clinical
therapeutic trial, for instance, is to obtain two groups of
patients so similar in all known relevant respects that any
difference in their responses can be reasonably attributed to
their different treatments. Not only sex and age but the type
and severity of the disease and its history, together possibly
with socioeconomic or lifestyle factors, if relevant, need to
be taken into account in ensuring the parallelism of the two
treatment groups. It is important that the full treatment regi-
men in both groups (experiment and control) be decided in
advance and adhered to precisely. There must be of course
a provision for emergencies, and therefore escape clauses
or alternative regimens should form part of the design of
the trial. A pilot trial, perhaps amounting to around 5% of
the full trial, can greatly help to reveal aspects previously
overlooked, and if the modifi cations it suggests are not too
great, it may be possible to include it as the start of the main
trial. For the reason that those directly concerned with the
conduct of the trial, or with its assessment, may form prema-
ture opinions about its outcome and hence introduce a bias if
they know the actual treatment that patients receive, it is cus-
tomary to run many clinical trials “blind”—that is, in such
a way that the clinicians are unaware of the treatment given.
If the active treatment consists of tablets, the control could
be a placebo presented in the same form; if it is an injection,
the control can receive an injection of normal saline; etc.
The trial may also be “double-blind,” when neither clinician
nor patient knows the identify of the “apparent” treatments.
Of course, a singly blind trial may imply that the patient is
unaware of his treatment but the clinician does know. There
are also occasions when the two treatments have differences
that cannot be distinguished, such as surgery for one and
radiotherapy for another.STRATIFICATIONWe have stressed already the importance of the close
similarity—almost identity—of the two groups of patients,
referring to obvious characteristics such as sex and age. Other
relevant features should also, if feasible, be similarly balanced
between the groups, and each of them may be described as a709 709Lung CancerSmoking1388801418688 65021 59++FIGURE 11C005_011_r03.indd 384C005_011_r03.indd 384 11/18/2005 10:25:43 AM11/18/2005 10:25:43 AM