Page 53 - Clinical Small Animal Internal Medicine

3 Using Data for Clinical Decision Making 21

divide it by the rate from drug B; this is called the inci- a particular treatment regimen by a veterinarian. This
VetBooks.ir dence rate ratio, which is often equivalently reported as type of bias is called “confounding by indication,” and all
nonrandomized studies of treatment efficacy are poten-
the hazard rate ratio or incidence density ratio. In this
example, the rate ratio = 0.29 / 0.11 = 2.7; this can be
trol for this bias, particularly in retrospective studies
interpreted to mean that the rate of cure from drug A is tially susceptible to it. The inability to statistically con-
2.7 times greater than the rate of cure from drug B, even where the reason for selecting a treatment may not be in
though the eventual probability of being cured is 100% in the medical record, should presumably dissuade
both drug groups. investigators from conducting nonrandomized studies of
When the rates in the two groups being compared are treatment efficacy.
identical, then no matter what those rates are, the rate
ratio will always equal 1.0. Typical significance tests that Case–Control Studies
are performed on such cohort data assume that the rate
ratio equals 1.0 – this is the “null hypothesis.” Rejection In one sense, a case–control study is a size‐ and cost‐effi-
of the null hypothesis (using a type I error proportion of cient variant of a cohort study. Both are longitudinal (ret-
5%) implies that the rate ratios at least as large (or small) rospective or prospective), can be performed on the
as those observed are unlikely (with a probability of less same population, and are designed to investigate how
than 5%) to have arisen when the null hypothesis and one or more potential measured risk factors may affect
model assumptions are correct – and thus the data are the occurrence of measured specified health outcomes
relatively incompatible with the null hypothesis. It is (such as becoming diseased). An important way in which
conventional to report rate ratio statistics accompanied they differ is in how populations are sampled for study
by: (1) their respective 95% confidence intervals to dem- inclusion. In cohort studies, investigators take a census
onstrate the degree of precision associated with the sta- of a population, unconditionally sample it, or sample it
tistic, and (2) P‐values corresponding to a test of the null conditional on risk factor status. In contrast, in case–
hypothesis that the rate ratio = 1 (i.e., there is no differ- control studies, investigators always sample conditional
ence in the rates of the outcome between the groups), on outcome (typically disease) status, selecting cases and
which are interpretable as the probabilities of finding controls. The studies also differ with respect to the sta-
rate ratios >1 at least as large (or rate ratios <1 at least as tistical interpretation of their respective effect measures.
small) as those observed in the study when the null Cohort studies, by virtue of their ability to estimate rates
hypothesis (of no difference in rates) is correct. and risks, allow the use of these statistics to construct
There are, however, compelling reasons not to use hos- comparative measures of putative effect, such as risk
pital‐based cohort studies to study treatment efficacy ratios and incidence rate ratios. Case–control studies,
between groups of patients. In contrast to intervention because of their unique sampling design, estimate odds
studies, where treatment is randomly assigned, cohort ratios (see Chapter 2 for a detailed explanation of this
study patients are intentionally (and, pointedly, non‐ran- statistic).
domly) administered a particular treatment by choice. For illustration, consider a study designed to test the
For example, one treatment may have been available dur- hypothesis that vaccination leads to a transient (two
ing earlier years of patient enrollment, but was later months) increase in the risk of IMHA in dogs. A hospi-
superseded by an alternative preferred treatment. A tal‐based cohort study could be undertaken by either: (1)
cohort study comparing these treatments would be una- enrolling some or all patients at risk of IMHA to the hos-
ble to discriminate between any possible effects they had pital, assessing their vaccination histories, and observing
and any effects related to time (such as from amended the subsequent incidence of IMHA conditional on vac-
standards of care, veterinarian experience and adeptness cination histories, or (2) conditionally enrolling dogs
at treating cases over time, different clinicians of poten- known to have been vaccinated and comparing them to
tially different abilities treating patients across times, enrolled dogs confirmed to have not received vaccines,
trends in disease severity seen over time at the hospital, and then measuring subsequent IMHA incidence. Both
etc.). In addition, clinicians administer treatments in approaches could be done retrospectively, provided vac-
part by using their acuity to judge patient severity; one cination histories were in the medical record and there
treatment may be indicated for milder cases, while an was sufficient patient follow‐up to determine if IMHA
alternative treatment, that may be more costly and risky occurred, or could be done prospectively by placing the
but potentially superior, may be earmarked for cases enrolled dogs with recorded vaccine histories under sur-
with the poorest prognoses. Again, it would be problem- veillance for disease onset.
atic for the investigator to distinguish whatever treat- The problem with this approach is that IMHA is a rela-
ment effects may exist that are distinct from the effects tively rare disease, and regardless of whether the cohort
of disease severity (or any other influences) that inspired study was done retrospectively or prospectively, it would