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3 Using Data for Clinical Decision Making 23

serve the same community. For economic reasons, some cause both the case and control conditions, then the fre-
VetBooks.ir pet owners utilize less expensive hospitals, and these quency distribution of exposure in the controls would
become more like that of the cases than of the source
owners are less likely (say, 50%, so assuming no month is
any more or less likely for vaccination the two‐month
specifically to an underestimation of the odds ratio. In
vaccination percentage is (2 months/12 months) × 50% = population of cases, leading again to a selection bias, and
8.3%) to provide consistent vaccination coverage for the IMHA example, one diagnosis would be particularly
their pets. In contrast, the pet owners who utilize the ill advised: patients diagnosed with immune‐mediated
investigator’s hospital are more likely (90%) to provide thrombocytopenia (IMTP). While vaccination may or
such vaccination coverage; their pets’ two‐month vacci- may not be associated with its etiology, the hypothesis
nation percentage is substantially higher: (2 months/12 that it could lead to IMHA leaves room for the possibility
months) × 90% = 15%, with an exposure odds of 0.15 / that it could lead to other immune‐mediated diseases
0.85 = 0.176 in the hospital-based controls. The odds affecting the bone marrow.
ratio relating two‐month prior vaccination to IMHA The choice of controls therefore necessarily depends
incidence is therefore 1.0 / 0.176 = 5.7, almost half that on a decidedly thorough and insightful understanding of
when using the random community controls. the relative benefits of particular control diagnoses for
This illustrates an important point of selecting con- particular exposures and case conditions; acceptable
trols for hospital‐based case–control studies: the source controls for one hypothesis or study may be unaccepta-
population of cases to be sampled as controls should be ble for another. Control selection is perhaps the most
restricted to those patients who, had they developed the contentious and challenging component of case–control
disease under study, would have gone to the same hos- study design, and should be carefully considered in
pital as the cases, and would have proceeded through advance of study commencement.
the same mechanism of diagnosis and case ascertain-
ment that occurred for the actual cases. There is no way Clinical Trials
to know whether such a hypothetical scenario would
actually hold when randomly sampling members of a The defining characteristic of these studies is their inter-
population; even asking the question of owners is con- ventional nature; unlike cohort studies, where treat-
jectural at best. ments are not under investigator control, in clinical trials
To accommodate this concern about selection bias, an investigators have the ability to randomly assign treat-
alternative approach involves selecting controls with ments to their patients in a way that allows valid estima-
particular diagnoses from the patient registry at the tion of their effects. Although many experimental
same hospital(s) or laboratory(s) that provide the cases. designs exist and have been adapted for clinical settings,
The singular advantage of this tactic is that whether or this section will focus on the two most common: the ran-
not an owner would utilize a particular hospital is no domized masked clinical trial, and the cross‐over trial.
longer an issue; what remains unknown, of course, is
what the owner would have done if their dog developed Randomized Masked Clinical Trials
the actual disease of interest. While this too is conjec- The drawback of using hospital‐based cohort studies to
tural, the choice of control diagnoses provides some evaluate treatment efficacy, as noted earlier, is that of
guidance, if not assurance. That is, if alternative diagno- confounding by indication; it is difficult, if even at all
ses could be identified for the case illness that are similar possible, to distinguish actual treatment effects from
with respect to severity of clinical signs to warranting the those of the underlying indications (which may or may
owner to seek medical assistance, cost of diagnosis, and not be consciously evident) for treatment choice.
owner propensity to seek diagnostic confirmation, then Random assignment of treatment, known as “randomi-
those patients may be acceptable as controls. Using the zation,” is the most powerful tool an investigator has to
IMHA example, diseases would be sought as control avoid this source of bias. The goal of randomization is
inclusion criteria that required presentation at the same beguilingly simple: to establish distinct but comparable
hospital, with similar laboratory work and diagnostic groups of individuals whose incidence of the outcome of
procedures performed as that of the cases. Many alterna- interest would be essentially identical if none received
tive diagnoses could potentially qualify. the treatment of interest. With such established groups,
An additional critical requirement to impose on con- it could then be possible to isolate the treatment’s effect
trols is that their medical condition should be unassoci- if administered to one of them [2].
ated with the exposure(s) of interest in the study (note: in Randomization itself is not a guarantee of group com-
this context unassociated means no more or less likely to parability, however. Consider two patients enrolled in a
be exposed than individuals in the source population; it study to compare a novel treatment to a placebo in treat-
does not mean unexposed). If this exposure were to ing a disease. Unknown to the investigator, one patient