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Department of Biostatistics, University of Washington, Seattle
In our article on the design of microbicide trials [1], we discuss 3 challenging issues. The first relates to the relative benefits of the use of both blinded and unblinded controls, including the need, in some settings, to consider the use of both. In response to 2 recent letters regarding our article [2, 3], we provide further clarification of the relative utility of these 2 types of controls.
The use of blinded controls provides a preferred approach in many clinical settings [1]. However, it is neither a "fundamental requirement" nor an "ironclad rule" that control groups be blinded. In fact, there are settings in which the use of blinded controls would not be ethical, such as when the interventions being compared are readily identifiable because of differences in risks of serious toxicities; for example, an experimental drug for the treatment of cancer may be known to induce high rates of significant adverse events, such as alopecia, stomatitis, myelosuppression, hepatic toxicity, or nausea and vomiting. In such settings, the use of unblinded controls has enabled unbiased evaluations of objective outcome measures, such as patient survival.
In some settings, such as when the placebo is not inert, the use of blinded controls may lead to biased results. In the setting of microbicides administered for the prevention of HIV infection, where there have been no trials with both blinded and unblinded controls, data do not exist that would reasonably reliably establish any placebo regimen to be inert. In fact, one might wonder whether the broadly unimpressive results that thus far have been reported for microbicide regimens evaluated in placebo-controlled trials are due, at least in part, to the fact that the placebo regimens could be carrying some important benefits of the microbicide regimen, including lubricating and/or physical-barrier effects, the presence of preservatives having microbicidal effects, the alteration of the vaginal microflora, or decreased concentrations of HIV-infected semen in the female genital tract. Unless an inert placebo is used, one is unable to obtain an unbiased estimate of efficacy.
There are additional settings in which the use of blinded controls may not lead to fully informative results, such as when one wishes to estimate the effectiveness of the intervention [1, 4]. But will estimates of effectiveness that are based on comparisons with unblinded controls be generalizable if (1) the study populations in clinical trials are "highly selected" or "totally unrepresentative" of the overall population at risk or (2) the adherence to study interventions does not match what could be expected in the real world In trials conducted under such conditions, neither a placebo-controlled estimate of efficacy nor an estimate of effectiveness based on a comparison with an unblinded control would be broadly generalizable. Participants selected for clinical trials should be a reasonable match with the population targeted to use the intervention in the real-world setting. Adherence to the experimental intervention (such as the use of topical microbicide) and to ancillary care (such as the use of condoms) should be similar to the best that is practically achievable in a real-world setting. Establishing the real-world benefit-to-risk profile of an intervention, rather than simply establishing "proof of concept," should be the goal of a registrational trial in a regulatory setting.
It has been suggested that one might evaluate efficacy in a registrational trial and defer the determination of effectiveness until after the intervention has been marketed. Yet, how would one conduct a post-marketing trial comparing a microbicide regimen having established efficacy against an unblinded "condom-only" control
Achieving high levels of retention also is an important issue in obtaining reliable conclusions. Will it be difficult to follow participants who are randomized to an unblinded "condom-only" control arm Fortunately, it has been possible to achieve high levels of follow-up, even for an unblinded standard-of-care regimen, in HIV-prevention trials in developing-country settings (see, e.g., [5, 6]). Interestingly, the recently completed HIVNET 015 trial followed 4350 participants for >3 years and had significantly higher rates of retention in the unblinded standard-of-care control arm than in the experimental behavioral-intervention arm [7].
Why shouldn't it be achievable to retain participants in an unblinded "condom-only" control arm All participants in clinical trials receive favorable quality of care, which is made possible by the resources committed to conducting the trial. Those participants randomized to the experimental microbicide regimen may or may not receive greater benefit. To date, no microbicide regimen has been established as being better than the nonmicrobicide control regimen. In fact, although it had been hoped that a high dosage of nonoxynol-9 delivered in a sponge covering the cervix would reduce the risk of HIV infection, it actually induced harm [8]. Hoping that an experimental microbicide regimen will provide improved protection is not the same as having scientific evidence to expect that it will be better. The informed-consent process should accurately convey equipoise regarding whether the experimental microbicide regimen or the control regimen truly provides the better benefit-to-risk profile. If this is done effectively, and if quality care is provided to all participants in a clinical trial, high levels of retention should be achievable in all randomization arms of the trial.
Compared with that of a trial having only a placebo control, will the power of a trial having dual controls be diminished because of "multiple comparison penalties" As has been discussed elsewhere [1], when dual controls are used, the power, appropriately, will be enhanced when effectiveness exceeds efficacy and, appropriately, will be diminished when effectiveness is less than efficacy.
We fully agree that there is urgent need for identification of an effective microbicide. To maximize the public-health benefit, the goal in the design and conduct of registrational clinical trials should be to obtain reliable as well as timely evaluation of the real-world benefit-to-risk profile of interventions.
References
1. Fleming TR, Richardson BA. Some design issues in trials of microbicides for the prevention of HIV infection. J Infect Dis 2004; 190:66674. First citation in article
2. Skoler S, Govender S, Altini L, et al. Risks of an unblinded study group . J Infect Dis 2004; 191:13778 (in this issue). First citation in article
3. Stein ZA, Susser MW. Control groups in microbicide trials: in defense of orthodoxy . J Infect Dis 2004; 191:13767 (in this issue). First citation in article
4. Padian N. Evidence-based prevention: increasing the efficiency of HIV intervention trials. J Infect Dis 2004; 190:6635. First citation in article
5. Guay LA, Musoke P, Fleming T, et al. Intrapartum and neonatal single-dose nevirapine compared with zidovudine for prevention of mother-to-child transmission of HIV-1 in Kampala, Uganda: HIVNET 012 randomised trial. Lancet 1999; 354:795802. First citation in article
6. Roddy RE, Zekeng L, Ryan KA, Tamoufe U, Tweedy KG. Effect of nonoxynol-9 gel on urogenital and chlamydial infection: a randomized controlled trial. JAMA 2002; 287:111722. First citation in article
7. The EXPLORE Study Team. Effects of a behavioral intervention to reduce acquisition of HIV infection among men who have sex with men: the EXPLORE randomized controlled study. Lancet 2004; 364:4150. First citation in article
8. Kreiss J, Ngugi E, Holmes K, et al. Efficacy of nonoxynol-9 contraceptive sponge use in preventing heterosexual acquisition of HIV. JAMA 1992; 268:47782. First citation in article