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This book is about creating a valid study, and a study must be unbiased to be valid, so in some sense this whole book is about ways to avoid bias. We highlight some of the important measures in this chapter, including population selection, randomization, and blinding, also referred to as masking.
18.1 Selection of Study Population
The choice of an appropriate population for a study is critical, yet it is sometimes difficult to locate and recruit participants for a study. Selection bias (Section 17.1.2) can be avoided by a realistic assessment of the populations that form the study pool and careful review of the criteria for inclusion and exclusion to ensure that it does not result in a biased population (Chapter 12).
It is up to you, the investigator, to use your best judgment: be honest with yourself as to what you can achieve. If you can only work with a limited population, then this must be acknowledged as a limitation in the presentation of the results of the study (Section 12.4). In Chapter 13 we gave some ways to reach potential participants outside your immediate environment.
Example 17C described a cohort study of the link between hormone therapy (HRT) and breast cancer. This study was considered biased because the women in the study were more likely to be at a higher risk for breast cancer and were more likely to be taking HRT than the general population. The Woman’s Health Initiative subsequently studied many of the same questions. There were 40 centers in different areas of the United States, including 20% minority enrollment. The investigators at each center had to devise plans for recruiting women in their entire geographical area, not just from their patient base, and for recruiting women with a diversity of health risk and health problems. The results of this study, which supported a link between HRT and breast cancer, were consistent across centers and were generally considered to be unbiased and representative of the U.S. population.
Often in a case-control study it is tempting to use the most readily available population as controls, but they may have demographic and economic characteristics that are not representative of the population at large. Although it might be easy to recruit graduate students and colleagues, they are a very select group in terms of age and education, and sometimes economically. This may result in a control population that differs from your cases in ways that are associated with the outcome of interest, and thus confound the comparisons of exposures.
Example 17B was a case-control study of adult males with a congenital hormone imbalance where controls were employees from the investigators’ institution and almost always had at least some kind of training certificate and often a bachelor’s degree or higher. The investigators thus also recruited a second control population from outside the institution in environments where they would expect to find a population that was more like the general population in cognitive function.
Recall bias is a common risk in a case-control study, because affected participants may have more reason to remember past events than do controls. One way to mitigate this effect is to select a control population that has characteristics that are different from the outcome of interest but that would still induce equal levels of recall.
Example 17J was a case-control study of prenatal events to determine their association with certain birth defects. It was believed that mothers with healthy infants would be less likely to recall events during the pregnancy than would the mothers of the cases. Therefore, the investigators added a second control group that consisted of mothers of infants who had birth defects different from those being studied.
Another way to minimize the effect of recall bias is to use a structured interview or questionnaire to ask about specific events, rather than just use open-ended questions. The interview may include specific methods to assist in recalling events.
The investigators were particularly interested in nutritional intake during pregnancy. The participants were asked what vitamin supplements they took and, if they had any left, to read the contents to the interviewer. They were also asked about the amount and frequency of eating other foods such as breakfast cereals and fortified bread.
Use of historical controls can introduce bias due to changes in methods of evaluation, such as assay methods or assessment instruments. Diagnostic criteria and the timing of diagnoses may be different. For example, many conditions may be identified earlier in the development of the disorder now than in the historical controls and more cases may be identified due to increased vigilance. Frequently there is limited information about the controls so that you may get summary statistics about age and sex but not the actual distribution or the age by sex distribution. We are generally not in favor of using historical controls for any study, and definitely not for an interventional study unless there is a uniform outcome from the disease. However, they might be used in observational studies if the investigator is careful to ensure that the populations are comparable in prognostic factors and exposures and that the outcomes of interest were evaluated using equivalent methods, but the use of historical control often raises concerns about potential bias.
18.2 Randomization
As we have stated in many places in this book, we believe that randomization is needed in interventional studies in all but the most extraordinary circumstances. Furthermore, we have never heard an investigator present an “extraordinary circumstance” that was not, ultimately, a way of saying it was too much work. This work is essential for a valid study. Randomization after enrollment is the single most effective way to rule out the possibility of prognostic bias. However, more than just random treatment allocation is needed: the treatment allocation cannot be assigned until after the participant is enrolled and completed screening for the study, and even then the actual treatment should be known by as few individuals as possible (see Section 18.3).
Consider the dilemma an investigator would have if the treatment assignment were known prior to enrolling and screening patients, for instance if the envelope containing the treatment allocation of the next participant had inadvertently been opened by an assistant. Suppose an investigator knew that the next participant would be given the experimental intervention. As is typical, this investigator believes that the experimental intervention will be more effective than the standard treatment being used in an interventional study, and his personal belief is that this is especially true for more severely affected individuals. The investigator has several patients scheduled as potential participants that day: the first is a patient with a relatively mild case, the second is a patient with a more severe case. The investigator knows that he needs to do everything possible to act the same to both patients when attempting to recruit them into the study. It will be extremely difficult for this investigator to do so, however, as he will feel it best if the first patient does not enroll and the second patient does, so that the second patient receives the benefit of the experimental therapy.
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