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In the January 2002 issue of the British Journal of Cancer, Sharpe and others published a case–control study reporting that the heavy use of certain tricyclic antidepressants (TCAs) is associated with an increased risk of breast cancer that follows a 10-year lag from the time of antidepressant use (1). The tricyclic agents implicated in the study are amoxapine, clomipramine, desipramine, doxepin, imipramine, and trimipramine (1). These results prompted a front-page newspaper article in the February 14, 2002, edition of The Globe and Mail, entitled “Research finds some depression drugs raise cancer risk” (2). The article stated that “certain kinds of antidepressants can double the risk of developing breast cancer, according to a landmark study . . . . Based on the finding, the lead researcher is recommending that physicians stop prescribing certain tricyclic antidepressants, and that women switch to drugs that do not risk damaging their DNA.” The article notes that “earlier research published by Michelle Cotterchio . . . found that at least one popular SSRI (Paxil) may increase the risk of cancer” (2). When interviewed for this article, Dr Cotterchio in fact stated that firm conclusions cannot be drawn from a single observational study; however, she was further quoted as stating that she would “switch antidepressants” if she were currently taking Paxil. This newspaper article and its quotations from the study authors have likely caused a considerable amount of anxiety, both in women who currently take antidepressant drugs and in women exposed to TCAs over past decades. Breast cancer is the leading cause of cancer among women worldwide (3). It comprises 30% of all newly diagnosed female cancers and 19% of all female cancer-related deaths. Although several risk factors for breast cancer are known—including substantial weight gain in postmenopausal women, delayed childbirth (young age at childbirth and multiparity are protective), alcohol consumption, benign breast disease, oral contraceptive use, positive family history in first-degree relatives, genetic risk (BRCA1 and BRCA2 genes), and, possibly, prolonged postmenopausal hormone replacement therapy (HRT)—they have a relatively weak association with breast cancer (4). Established risk factors account for less than one-half of all cases (5), suggesting that other unknown factors may be important. In calling for physicians to avoid prescribing the implicated tricyclic agents, based upon the results of his study, Dr Sharpe implies that current evidence is sufficiently strong to recommend clinical actions. Although Dr Cotterchio’s message is more ambiguous, the abstract to her study concludes that “paroxetine may be associated with a substantial increase in breast cancer risk.” (6). Given the strength of these claims and their potential influence upon the treatment decisions of many women, we have critically reviewed these 2 studies to determine how strongly the evidence and analyses presented support the authors’ recommendations. We summarize the important methods and findings of each study and evaluate the relative strengths and weaknesses of the methods. We conclude by recommending directions for future research and by considering what clinical practices, if any, should be modified, based upon the studies’ results. Sharpe and Others, 2002 (1)This paper reports findings from a population-based case–control study that used 2 linked administrative databases: the Saskatchewan Drug Prescription Plan (SPDP) and the Saskatchewan Cancer Agency (SCA). As with all case–control studies, the primary analytical objective is to determine the risk of breast cancer in women exposed to TCAs, compared with a control population of women not exposed to TCAs. This relative risk is typically expressed in terms of an odds ratio (OR). The population sampled in the study included women aged 35 years and older who were eligible for SPDP benefits during the period 1981 to mid-1995. From the SPDP, the authors extracted data pertaining to TCA exposure, measured as both dosage and duration of use. From the SCA, the authors identified “cases” as histologically proven diagnoses of breast cancer. The study’s analyses were based upon 5887 cases and 23 517 control subjects chosen randomly from the eligible age-matched control population. All analyses were age-matched and controlled for the effects of TCA exposure at multiple past time intervals, but the study did not control for other potential confounding factors. Exposure to TCAs was calibrated based on accumulated dosage and the time interval prior to diagnosis or on duration of exposure (expressed as the percentage of time that TCA prescriptions were filled during the total years of potential exposure). Multiple statistical comparisons were made, classifying study women by the recentness and total amount of TCA exposure. Based upon an initial positive finding, the authors conducted a further post hoc analysis contrasting TCAs classified as genotoxic with those classified as nongenotoxic. TCAs were classified as genotoxic based on studies that demonstrated abnormal Drosophila wing development after exposure to certain molecularly similar TCAs (7,8). The results of the analyses are provocative. Overall, there was a similar prevalence of TCA use in cases and control subjects (18.7% vs 18.6%). In women with less than 10 years separating TCA exposure and breast cancer diagnosis, there was no association at any dosage. However, a significant increase in the relative risk of breast cancer was associated with TCA exposure in women with more than 10 years’ exposure prior to diagnosis, and only at the highest accumulated exposure category. In this time period, the crude relative risk ratio (RR) (Note 1) for breast cancer in the highest TCA dosage category was 2.14 (95%CI, 1.45 to 3.17; adjusted RR 2.02; 95%CI, 1.34 to 3.04), and the adjusted RR at the greatest duration of exposure was 1.52 (95%CI, 1.34 to 3.04). Post hoc analyses showed no increased risk of breast cancer associated with nongenotoxic TCAs. However, there was an increased risk of breast cancer associated with exposure to genotoxic TCAs 11 to 15 years prior to diagnosis at the second-highest (adjusted RR 1.93; 95%CI, 1.25 to 2.99) and highest dosages (adjusted RR 2.47; 95%CI, 1.47 to 4.40). There was no increased risk of breast cancer associated with genotoxic or nongenotoxic TCA exposure within 10 years of diagnosis. The study by Sharpe and others (1) is an example of the increasing use of administrative databases to test clinical hypotheses. There are 3 distinct advantages to this approach: large sample sizes, minimization of selection bias, and virtual elimination of recall error and recall bias. Large sample sizes carry the usual advantages of statistical power and also create opportunities for subgroup analyses. Selection bias occurs when cases and control subjects are chosen in a biased manner that results in determinants of outcome that differ between the groups from the determinant under study. Selection bias is minimized in this study because the SPDP provides prescription drug coverage to virtually all Saskatchewan residents, and the SCA captures all histologically confirmed cases of cancer in the province. Recall error occurs when study subjects inaccurately recall details of past exposures (in this case, TCA use). This phenomenon is known to occur widely among survey respondents. Recall bias occurs when case subjects systematically recall details of exposures and outcomes differently from control subjects. For example, this could happen if case subjects diagnosed with breast cancer were more or less likely to recall details of past antidepressant treatment than were control subjects. While recall problems can plague case–control studies, they are not a concern here. Despite the strengths of Sharpe and others’ research design, there are several limitations related to potential confounding, multiple statistical comparisons, and post hoc analyses. In our opinion, these limitations were not sufficiently acknowledged or explicated in the published paper or by the author in the newspaper article. An objective of all case–control studies is to reduce the likelihood that observed associations are caused by confounding. As stated in the introduction, there are several known risk factors for breast cancer, although none of these have strong predictive value (4,5). Nonetheless, known risk factors should as much as possible be accounted for, either as matching variables for case and control subjects or by multivariate statistical methods. Administrative data limitations may have prevented the investigators from controlling for all known confounders, but the paper is silent regarding these issues. It is unclear, for example, why exposure to oral contraceptives could not have been included in the analysis, since the administrative data sources used in the study presumably captured this information. In addition, the paper offers no descriptive results based on comparisons of case and control subjects’ observed demographic characteristics. Including such data assists readers to decide whether the case and control populations are meaningfully comparable. A further difficulty with this research paper is its failure to make adjustments for multiple statistical comparisons. This issue will be familiar to many readers, but it is worth repeating here. On the most parsimonious count, the results of the paper’s Tables 2 and 3 indicate that 30 or more separate statistical tests were performed. As the number of statistical tests rises, the probability of wrongly rejecting the null hypothesis (that is, declaring an association to be significant, when in fact it is spurious and based upon chance) increases. A simplified example illustrates this phenomenon. For an experiment with 20 independent statistical tests, with each test nominally assigned a standard a level of 0.05, the probability of finding at least 1 spurious association is 64%—a probability that increases to 79% with 30 tests. The statistical issues involved in multiple statistical comparisons are complex (9), and they have motivated a wide range of proposed statistical solutions, including conservative and straightforward methods such as the Bonferroni correction. Our purpose here is not to impose a statistical remedy but to take issue with the omission from the paper’s methods and discussion sections. While any reasonable method of adjusting for multiple tests would not have affected the point estimates of the paper (that is, the RRs themselves), it would certainly have widened the CIs and erased the “significant” associations reported. Finally, we suggest that the study findings be placed in their proper context. The most provocative result is the reported association between TCA exposure and breast cancer, found only in those cases with at least a 10-year interval between exposure and disease. This finding is provocative for 2 reasons. First, it appears to have biological plausibility, based upon current models of carcinogenesis and the timing of disease progression. Second, it appears that the finding emanates from a priori hypotheses held by the investigators; that is, hypotheses formulated in advance of the research. Results based upon a priori hypotheses are generally more convincing, because they are less prone to the bias and “data mining” that can take place with post hoc analyses. However, the supplementary findings of the paper—that the association between TCAs and breast cancer in fact relate to a subgroup of TCAs—appear to be the result of a post hoc analysis. Post hoc analyses are common and appropriate in exploratory research. Further, they can generate findings that suggest avenues for future research. However, such analyses are also more subject to bias.
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