Correspondence to: Sholom Wacholder, PhD, Biostatistics Branch, Division of Cancer Epidemiology and Genetics, National Cancer Institute, Bethesda, MD 20892-7244 (e-mail: wacholder{at}nih.gov)
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ABSTRACT |
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INTRODUCTION |
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Consequently, much of the published information on the efficacy of interventions intended to reduce the risk for disease comes from retrospective analyses of the medical records of individuals enrolled at high-risk clinics (i.e., clinics that counsel and treat patients who are at high risk for a particular disease). Retrospective studies of women from high-risk clinics that focus on BRCA1 and BRCA2 mutation carriers, who are at increased risk of breast and ovarian cancers, have evaluated the effects of potential interventions such as oophorectomy (911), mastectomy (12), tubal ligation (13), pregnancy (14), and the use of oral contraceptives (15,16) and tamoxifen (17). Here I describe a potential bias that may arise in studies that use populations from high-risk clinics to examine the effects of an intervention on risk.
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Advantages and Disadvantages of Clinic-Based Studies |
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Prospective follow-up of everyone seen at the clinic beginning at the time of first enrollment or when mutation carrier status is determined (48) is ideal. However, because a prospective study design may yield only small numbers of patients and short duration of follow-up, many retrospective clinic-based studies allow prevalent patients, i.e., those diagnosed with disease before being seen at the clinic, to be case patients.
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Bias |
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The following hypothetical example shows how including case patients diagnosed before being seen at the clinic but requiring all control subjects to have been seen at the clinic could introduce bias. A BRCA1 or -2 mutation carrier diagnosed with breast cancer in 1990the first member of her family to be affectedis included in a casecontrol study as a case patient. Clearly, this woman's family history gave her no reason to suspect that she was at increased risk, so she would not have undergone a surgical, medical, behavioral, or early detection intervention for prophylaxis before her breast cancer diagnosis. On the other hand, her sister, who was seen at the same clinic and identified as a mutation carrier in 1998, perhaps after yet another sister had been diagnosed with ovarian cancer, might have been urged to consider undergoing an intervention to reduce risk specifically because of her sisters histories and genetic test results. Thus, in the absence of an effect of the intervention, the case patients (e.g., women diagnosed with breast cancer in 1990) would be less likely to receive the intervention than potential control subjects (e.g., their unaffected sisters), and the intervention will appear protective. If the intervention does have a protective effect, the protection will be exaggerated; the negative effect of a deleterious intervention will be attenuated or possibly appear protective.
Table 1 presents a simple numerical example that illustrates how selection bias can create a false impression of benefit from an intervention in a clinic-based study. Consider a casecontrol study of the effect of an ineffective intervention received by 10% of the general population, regardless of their carrier status, family history of disease, or other determinants of risk. Furthermore, assume that half of carriers enrolling at the clinic without previous exposure to the intervention receive the intervention immediately upon enrollment and that the other half never receives the intervention. Then, 10% of 100 case patients diagnosed before going to the clinic and 55% [i.e., 10% + (50% x 90%)] of 100 case patients diagnosed after being seen at the clinic will have been previously exposed to the intervention at the time of diagnosis. Thus, 65 (32.5%) of 200 case patients will have been exposed to the intervention at the time of diagnosis. By contrast, 55% of the 200 control subjects drawn from clinic visitors will be exposed to the intervention. Thus, the odds ratio for the intervention would be 0.39 [i.e., (0.325/0.675)/(0.55/0.45)], suggesting protection, even though there was no benefit. Notice that in this scenario, there would be no selection bias if case patients and control subjects were restricted to individuals who were never seen at the clinic; the frequency of intervention would be 10% in each group. Similarly, there would be no selection bias if the case patients and control subjects were restricted to those who had not received the intervention before they enrolled in the clinic (because the frequency of intervention would be 50% for each group). Although only someone previously seen at the clinic can be selected as a control subject, a patient can be included as a case without having been seen at the clinic before diagnosis. Because having been seen at the clinic also is related to the probability of having received the intervention, epidemiologic theory says that this flawed study design is susceptible to selection bias (18).
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The magnitude of the overestimate of benefit from the intervention in this constructed example is probably extreme. However, it is not usually possible to quantify the bias in an actual study without having the investigators provide information about how many cases were prevalent at enrollment at the clinic and the percentage of unaffected enrollees who receive the intervention at the clinic. There is, however, some information about both prospective-only and retrospective-only analyses in the recent study from the Prevention and Observation of Surgical Endpoints Study Group on the effects of prophylactic mastectomy on the risk of breast cancer (6). It is telling that the only two cases of breast cancer observed in women with a history of bilateral mastectomy, as well as 130 (87%) of the 149 breast cancer cases in women without mastectomy, needed to be excluded from the prospective analysis (referred to as "analysis 4") (6).
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General Principle |
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Because a casecontrol study is simply an efficient way to study the same cohort, a proper casecontrol study should adhere to the same eligibility restrictions and exposure definitions as a cohort study (18). If all control subjects were previously enrolled at the clinic, only those cohort members affected after being seen at the clinic should be included as case patients. When unaffected patients seen at the clinic are more likely to receive the intervention, the bias is more severe.
A retrospective approach can be adequate for cofactors that do not vary with time, such as germline DNA. But the value of the exposure defined by "history of intervention" can increase from 0 to 1, perhaps quite frequently immediately after an unaffected patient is first seen at the clinic. It is also important, of course, that the time of evaluation of case patients and control subjects exposures be comparable.
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Evaluating Effects of Interventions Received at a Clinic |
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Hartmann et al. (12) took a different approach in their study of the efficacy of bilateral prophylactic mastectomy in BRCA1 and BRCA2 gene mutation carriers. They did not try to monitor women who did not receive an oophorectomy for occurrence of cancer cases. Instead, they estimated the efficacy of the intervention by comparing the number of cases they observed in follow-up of women who received an oophorectomy to the number of cases expected in the absence of oophorectomy; the expected number of cases was calculated on penetrance estimates (1921). The validity of this method depends on how close the penetrance models are to the rates that would be observed in patients seen at the clinic had they not received oophorectomy.
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CONCLUSIONS |
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Several other biases may occur in studies of the effect of prophylactic surgery and other interventions in mutation carriers. Klaren et al. (22) identified, among others, "confounding by indication" (i.e., when individuals at greater risk are more likely to receive the intervention than individuals at lower risk) and "informative censoring" (e.g., censoring by death from ovarian cancer in a study whose endpoint is breast cancer). Additionally, use of prevalent cases can lead to a second bias. Patients with lengthy survival time after diagnosis will be overrepresented among case subjects. If the exposure affects survival time, the effect of exposure on risk of disease can be distorted.
There is not enough information available from published reports to quantify the bias at this point. It is likely, however, that bias is substantial in those clinic-based investigations in which a large fraction of case patients were diagnosed before being seen at the clinic and in which there is a large increase in frequency of the intervention among those seen at a clinic. Indeed, Rebbeck et al. (6) reported that a large fraction of the cases was identified retrospectively. It seems likely that personnel at high-risk clinics are quite persuasive at encouraging their already-predisposed patients to take interventions, so enrollment at the clinic is likely to affect the chance of receiving the intervention. Published reports of findings from such studies should include sufficient information to allow the reader to evaluate these potential biases.
In conclusion, when mutation carriers diagnosed before they have enrolled at a high-risk clinic are included as case patients and only unaffected mutation carriers seen at the clinic are included as control subjects, reports of interventions commonly given in high-risk clinics may have a substantial bias toward overestimating efficacy. This bias may render these studies too flawed to serve as the basis for patient management decisions in the decade or so before clear evidence from randomized trials of interventions to reduce the risk of disease is available. Although population-based cohort or casecontrol studies can provide some useful information, these studies are difficult to launch because mutation carriers are rare and difficult to identify, and analyses of these studies have limitations (23) even when feasible (1,2). For example, the discrepancy in the published data (1,15) about whether oral contraceptives exert a protective effect among BRCA1 and BRCA2 mutation carriers suggests that we may not yet have definitive answers to these important clinical questions. Investigators of clinic-based studies must either avoid including patients diagnosed before being seen at the clinic or show that the resulting bias has limited impact before clinic-based studies can reliably guide critical management decisions for persons at increased genetic risk for cancer.
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REFERENCES |
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1 Modan B, Hartge P, Hirsh-Yechezkel G, Chetrit A, Lubin F, Beller U, et al. Parity, oral contraceptives, and the risk of ovarian cancer among carriers and noncarriers of a BRCA1 or BRCA2 mutation. N Engl J Med 2001;345:23540.
2 Rutter JL, Wacholder S, Chetrit A, Menczer F, Ebbers S, Tucker MA, et al. Gynecologic surgeries and risk of ovarian cancer in women with BRCA1 and BRCA2 Ashkenazi founder mutations: an Israeli population-based case-control study. J Natl Cancer Inst 2003;95:10728.
3 Modugno F, Moslehi R, Ness RB, Nelson DB, Belle S, Kant JA, et al. Reproductive factors and ovarian cancer risk in Jewish BRCA1 and BRCA2 mutation carriers (United States). Cancer Causes Control 2003;14:43946.[CrossRef][ISI][Medline]
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6 Rebbeck TR, Friebel T, Lynch HT, Neuhausen SL, van 't Veer L, Garber JE, et al. Bilateral prophylactic mastectomy reduces breast cancer risk in BRCA1 and BRCA2 mutation carriers: the PROSE Study Group. J Clin Oncol 2004;22:105562.
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9 Rebbeck TR, Levin AM, Eisen A, Snyder C, Watson P, Cannon-Albright L, et al. Breast cancer risk after bilateral prophylactic oophorectomy in BRCA1 mutation carriers. J Natl Cancer Inst 1999;91:14759.
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12 Hartmann LC, Sellers TA, Schaid DJ, Frank TS, Soderberg CL, Sitta DL, et al. Efficacy of bilateral prophylactic mastectomy in BRCA1 and BRCA2 gene mutation carriers. J Natl Cancer Inst 2001;93:16337.
13 Narod SA, Sun P, Ghadirian P, Lynch H, Isaacs C, Garber J, et al. Tubal ligation and risk of ovarian cancer in carriers of BRCA1 or BRCA2 mutations: a case-control study. Lancet 2001;357:146770.[CrossRef][ISI][Medline]
14 Jernstrom H, Lerman C, Ghadirian P, Lynch HT, Weber B, Garber J, et al. Pregnancy and risk of early breast cancer in carriers of BRCA1 and BRCA2. Lancet 1999;354:184650.[CrossRef][ISI][Medline]
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17 Narod SA, Pal T, Graham T, Mitchell M, Fyles A. Tamoxifen and risk of endometrial cancer. Lancet 2001;357:656.[CrossRef]
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19 The Breast Cancer Linkage Consortium. Cancer risks in BRCA2 mutation carriers. J Natl Cancer Inst 1999;91:13106.
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21 Struewing JP, Hartge P, Wacholder S, Baker SM, Berlin M, McAdams M, et al. The risk of cancer associated with specific mutations of BRCA1 and BRCA2 among Ashkenazi Jews. N Engl J Med 1997;336:14018.
22 Klaren HM, van't Veer LJ, van Leeuwen FE, Rookus MA. Potential for bias in studies on efficacy of prophylactic surgery for BRCA1 and BRCA2 mutation. J Natl Cancer Inst 2003;95:9417.
23 Albert PS, Ratnasinghe D, Tangrea J, Wacholder S. Limitations of the case-only design for identifying gene-environment interactions. Am J Epidemiol 2001;154:68793.
Manuscript received November 6, 2003; revised June 9, 2004; accepted June 28, 2004.
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