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Letters To The Editor |
aAnkara University School of Medicine, Department of Obstetrics and Gynecology, Ankara, Turkey; bDivision of Biostatistics and Epidemiology, Department of Public Health, Weill Medical College of Cornell University, New York, New York, USA; cDepartment of Obstetrics & Gynecology, New York Medical College, Valhalla, New York, and Institute for Fertility Preservation, Center for Human Reproduction, New York, New York, USA
Correspondence: Kutluk Oktay, M.D., Institute for Fertility Preservation, Center for Human Reproduction, 21 E. 69th Street, New York 10021, New York, USA. Telephone: 212-994-4400; Fax: 212-994-4499; e-mail: kutluk.oktay{at}kutlukoktay.com; Website: http://www.fertilitypreservation.org; http://www.centerforhumanreprod.com
Received March 5, 2008; accepted for publication March 12, 2008.
Disclosure: No potential conflicts of interest were reported by the authors.
We would like to thank Dr. Somers and colleagues for their contribution to our debate on the efficacy of gonadotropin-releasing hormone (GnRH) analogues in fertility preservation. Somers et al. purport that fertility and menstruation are separate functions of the ovary and that GnRH analogues may preserve the latter without having an effect on the former. While the presence of menstruation is not a sign of fertility [1], it is biologically implausible that a drug that does not preserve fertility can delay menopause. The root cause of ovarian failure is the exhaustion of the primordial follicle reserve, also referred to as the ovarian reserve. When the number these follicles falls below a critical value, both fertility and menstrual function are altered [2, 3]. Amenorrhea is only the last benchmark in that process. Because estrogen and progesterone production requires a functional follicle, and because those follicles originate from the ovarian reserve, it may not be plausible that GnRH analogues can preserve hormonal function while they do not preserve fertility—that is, unless GnRH analogue treatment is delaying the inevitable, that is, delaying the clearance of follicles already damaged from chemotherapy.
There is some evidence to support the latter possibility. (a) In electron-microscopic studies, surviving follicles were morphologically abnormal postchemotherapy and were eventually cleared from the ovary [4]. (b) Fox et al. [5] encountered an extremely poor obstetrical outcome in women who received GnRH analogues during chemotherapy and abandoned the use of these agents for fertility preservation. (c) A recent observational study showed that, despite lower amenorrhea rates in the GnRH analogue–treated group, ovarian reserve markers (anti-Müllerian hormone, antral follicle count, follicle-stimulating hormone [FSH], and inhibin B) were not different than in the controls [6].
A more likely explanation is, however, that because none of these studies were randomized and prospectively followed, various biases in patient recollection and selection might have favored a positive outcome in the intervention group. Patients who ask for a GnRH analogue are highly motivated to preserve gonadal function and thus they may be more likely to recall menstrual activity or interpret any vaginal bleeding as menstruation. The use of add-back estrogen treatments further confounds the analysis of the effectiveness of GnRH analogues, because such treatments would spuriously lower FSH levels and may result in menstrual activity, both of which can give the impression that gonadal function has been preserved. Treatment selection and adherence mechanisms are indeed highly complex and difficult, if not impossible, to characterize in most nonrandomized or observational studies. Contradictory findings and ensuing huge debates on the effectiveness of some treatments, such as hormone replacement therapy and vitamin E, can be understood within the same context [7].
We understand there are some controversies in post hoc power calculation. The statistical paper that Somers et al. cited provides a warning that we should not (mis)use power calculation when we reach an insignificant result by attributing it to insufficient power. In that paper, Hoenig and Heisey [8] did not claim that power should not be assessed or considered at all based on the observed data after the study is over. They were also concerned about the overemphasis on p-values and hypothesis testing in current practice. Statistical power is oftentimes all based on assumptions in the lack of reliable preliminary data or previous studies. When a study is actually conducted or completed, there are various reasons not to attain the power we originally hoped with the sample size we used. We believe that a post hoc power calculation is still valid for power assessment based on the observed data, if appropriately used and interpreted. (Actually, other researchers may use the estimates you observe as a preliminary study in the future!) Most importantly, low power is still low power regardless of whether it is calculated prestudy or poststudy.
Along this line, we are curious how/why Somers et al. chose a 1:1 ratio for case:control (total sample size of 40). Unless it is very difficult to find controls, two to four controls per case are generally encouraged in order to make controls better represent the control population, to increase power, and to lend credibility to the results. Retrospective studies are vulnerable to many causes of bias; in particular, when the time-to-event data, which are better suited for prospective studies, are used for a survival analysis, great care should be exercised in assuring sample comparability. Because of nonrandomization, it is important to understand the characteristics of the patients treated using the study intervention (the so called propensity in statistics and epidemiology). Also, Somers et al. cited a meta-analysis of observational studies, but such an analysis presents particular challenges because of inherent biases and differences in study design, so cautious interpretations of treatment efficacy/effectiveness along with some sensitivity analysis are mandatory [9–11]. We need to pay special attention to meta-analyses based on observational studies, because combining incorrect stories can create more serious problems than reporting a single incorrect story and publication bias could be severe [12–14].
Finally, we are not sure if GnRH analogue treatment is "10" times more effective in reducing the risk for ovarian failure, compared with controls, and if this hazard ratio is an unbiased estimate of the true effect, and if this estimate will be reproduced in future studies, especially well-designed and managed RCTs that will estimate average causal effects. Not only the statistical significance and acceptance/rejection of a hypothesis, but also the magnitude of point and interval estimates, are important. If overestimation ever occurred, various factors inherent in the observational studies, in addition to the treatment itself, would be responsible.
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AUTHOR CONTRIBUTIONS |
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Collection/assembly of data: Murat Sönmezer, Kutluk Oktay
Data analysis and interpretation: Murat Sönmezer, Heejung Bang, Kutluk Oktay
Manuscript writing: Murat Sönmezer, Heejung Bang, Kutluk Oktay
Final approval of manuscript: Murat Sönmezer, Kutluk Oktay
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