10
Alternative Designs

Late-stage biomedical HIV prevention trials have mostly used superiority designs to compare a new biomedical intervention, such as a PrEP antiretroviral or a microbicide gel, to a control arm—often a placebo—with subjects in both arms receiving risk-reduction counseling. Such trials aim to advance the field by assessing whether the new intervention is superior to a standard prevention method, with the expectation that if the trial is positive, it might change practice.

This approach is commonly used to evaluate new interventions in a wide variety of prevention and treatment trials. However, the committee believes that use of alternative types of superiority trials as well other types of trial designs, which also have been used in other settings, can offer important advantages for certain nonvaccine biomedical HIV prevention studies.

First, product adherence and risk behavior are important determinants of the effectiveness of a biomedical HIV prevention intervention, but these factors can vary substantially across populations and individuals (see Chapter 5). This variability can complicate the interpretation of prevention studies using a superiority design, because the “average” intervention effect may not apply to different subpopulations with different risk behaviors and adherence patterns. This argues for studies that can identify improved ways of improving adherence and/or reducing high-risk behavior, or tailor an individual’s intervention to provide the maximal amount of protection against HIV infection that is available with current interventions.

Similarly, although investigators conducting late-stage biomedical HIV prevention trials are ethically required to provide all participants with



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10 Alternative Designs L ate-stage biomedical HIV prevention trials have mostly used superi- ority designs to compare a new biomedical intervention, such as a PrEP antiretroviral or a microbicide gel, to a control arm—often a placebo—with subjects in both arms receiving risk-reduction counseling. Such trials aim to advance the field by assessing whether the new interven- tion is superior to a standard prevention method, with the expectation that if the trial is positive, it might change practice. This approach is commonly used to evaluate new interventions in a wide variety of prevention and treatment trials. However, the commit- tee believes that use of alternative types of superiority trials as well other types of trial designs, which also have been used in other settings, can offer important advantages for certain nonvaccine biomedical HIV prevention studies. First, product adherence and risk behavior are important determi- nants of the effectiveness of a biomedical HIV prevention intervention, but these factors can vary substantially across populations and individuals (see Chapter 5). This variability can complicate the interpretation of prevention studies using a superiority design, because the “average” intervention effect may not apply to different subpopulations with different risk behaviors and adherence patterns. This argues for studies that can identify improved ways of improving adherence and/or reducing high-risk behavior, or tailor an individual’s intervention to provide the maximal amount of protection against HIV infection that is available with current interventions. Similarly, although investigators conducting late-stage biomedical HIV prevention trials are ethically required to provide all participants with 0

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0 ALTERNATIVE DESIGNS risk-reduction counseling and other prevention interventions (e.g., access to free condoms), there is limited experimental evidence on the relative effectiveness of behavioral risk-reduction interventions in many of the set- tings where biomedical trials are conducted (see Chapter 3). One way to advance knowledge in this area is to incorporate evaluations of behavioral risk-reduction interventions into the design of biomedical HIV prevention trials. In addition, no single preventive intervention is likely to have a sub- stantial and sustained protective effect. Designs that allow investigators to determine optimal combinations of interventions—including both biomedi- cal and behavioral components—therefore hold greater promise for slowing the epidemic, even though using different combinations in one trial can complicate the evaluation process. The “optimal” intervention is also likely to vary among individuals based on the nature of their exposure to HIV. For example, some women may have difficulty negotiating certain forms of prevention, such as condom use. Designs that allow access to alternative forms of protection could be more effective in reducing the risk for these individuals. Finally, given the complex dynamics among members of a community in the transmission of HIV, some intervention trials, such as trials involving behavioral risk-reduction interventions, might be better suited to random- izing groups of subjects rather than individuals. And further, when feasible, there can be important advantages to designs that enroll HIV-discordant couples to assess the protective effectiveness of interventions in settings where the main, and sometimes sole, HIV exposure of the uninfected part- ner is known. The committee believes that these considerations suggest the need for investigators to explore alternative study designs that test multiple preven- tive interventions, including multiple behavioral risk-reduction interven- tions and strategies to improve product adherence. Ideally these strategies could be individualized to reflect changes in people’s behavior and adher- ence over time. This chapter reviews the advantages and disadvantages of several alternatives to the traditional superiority design including facto- rial and other multiarm designs, noninferiority designs, discordant couple designs, cluster randomization designs, and dynamic designs. FACTORIAL AND OTHER MULTIARM DESIGNS Treatment trials commonly use factorial designs to investigate the value of two or more types of interventions. To illustrate, consider a 2 × 2 facto- rial design with two types of interventions, for example A and B, each of which can be given at one of two levels (e.g., A1 or A2 and B1 or B2). Subjects are randomized to one of the four (2 × 2) combinations of

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0 METHODOLOGICAL CHALLENGES IN HIV PREVENTION TRIALS interventions; that is, to A1 + B1, A1 + B2, A2 + B1, or A2 + B2. For example, if the levels of A (or B) include getting intervention A (or interven- tion B) versus getting a placebo for intervention A (or B), the arms of the trial would be as follows: Arm 1: A1 + B1 = Intervention A combined with Intervention B Arm 2: A1 + B2 = Intervention A combined with Placebo B Arm 3: A2 + B1 = Intervention B combined with Placebo A Arm 4: A2 + B2 = Placebo A combined with Placebo B This design need not necessarily involve a placebo alternative to each factor. Thus, the A component could entail offering some participants a biomedical intervention and no other intervention (without a placebo), while B could entail offering some participants a more intense behavioral risk-reduction intervention and offer others standard risk-reduction coun- seling, in which case subjects would be unblinded with respect to both their biological and behavioral interventions. Or, in A, some participants may receive a biomedical intervention while others receive a placebo of this intervention, as in the original example, while some subjects in B might receive either a new behavioral risk-reduction intervention while others receive standard risk-reduction counseling. Here, subjects will be blinded to their biological intervention but not to their behavioral risk-reduction intervention. This is called a partially blinded factorial design. Although this example focuses on intervention strategies to reduce risk-taking behavior, the designs also apply to evaluating and comparing strategies aimed at improving adherence. Factorial designs are motivated by an assumption of “no interaction” between the two interventions. Simply put, this means that the relative benefit of intervention A in the absence of intervention B is the same as the relative benefit of intervention A in the presence of intervention B. In the above example, if the intervention effect is measured by relative risk (RR), the assumption of no interaction means that the RR of intervention A to placebo A in subjects who receive placebo B is the same as the RR of inter- vention A to placebo A in subjects who receive intervention B. That is, the incremental benefit of adding intervention A (in this example measured by RR) is the same in the presence or absence of intervention B. For example, if the risk of becoming HIV infected is 0.10 or 0.02, depending on whether intervention B is or is not used, and the RR of A is 0.5, then the risk of becoming infected is 0.01 (0.5 × 0.02) if both A and B are used, and is 0.05 (0.5 × 0.10) if only A is used.

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0 ALTERNATIVE DESIGNS Quantitative vs. Qualitative Interactions Interactions are sometimes classified as quantitative versus qualitative. In a quantitative interaction, receiving intervention A is better than not receiving it for each level of B, but the magnitude of the benefit varies. For example, intervention A might reduce the risk of HIV infection by 30 percent in individuals receiving intervention B, but reduce it by 50 percent in subjects who do not receive intervention B. Quantitative interactions might be expected to occur in a trial where A represents a biomedical intervention or its placebo, and B represents two behavioral risk-reduction strategies. The basis for anticipating that there would be either no interaction or a quantitative interaction in this setting is based on the fact that the biological intervention is blinded to study sub- jects. Thus, while the two intervention strategies could modify risk behavior and thus HIV infection risk in different ways, the “better” behavioral risk- reduction intervention strategy would not depend on whether a subject is receiving A or its placebo. If the biomedical intervention were efficacious, one would expect it to be effective, though possibly by different amounts, in subjects receiving either of the behavioral risk-reduction interventions. In contrast, an example of a qualitative interaction is one in which receiving intervention A is better than not receiving it for one level of B but worse for the other level of B. For example, when A denotes a biomedical intervention and B denotes two behavioral risk-reduction interventions, a qualitative interaction would occur if intervention A reduced risk in sub- jects who receive one behavioral risk-reduction intervention but increased risk in subjects receiving the other behavioral intervention. Such outcomes may not be implausible when A is an unblinded comparison (for example, of receiving intervention A versus not receiving intervention A), as knowl- edge of whether a participant is receiving A could affect her or his response to the different behavioral risk-reduction interventions. For example, if B denotes intense versus standard risk-reduction coun- seling, disinhibition might occur in subjects who receive standard counsel- ing. The result could be that subjects who receive a marginally efficacious biomedical intervention (A) have a higher HIV infection rate than subjects who do not receive A. Meanwhile subjects who receive more of an inten- sive behavioral risk-reduction intervention may have no disinhibition, so subjects receiving A have a lower infection rate than those not receiving A. The interpretation of a trial with a qualitative interaction is usually more complicated than when there is no interaction or only a quantitative interaction.

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0 METHODOLOGICAL CHALLENGES IN HIV PREVENTION TRIALS Sample Size and Analysis of Factorial Designs If the assumption of no interaction holds, the attractiveness of a 2 × 2 factorial design is that it can evaluate two different interventions (e.g., microbicide versus placebo gel and enhanced versus standard counseling) with the same sample size as a trial investigating only one of the interven- tions (e.g., microbicide versus placebo gel). The benefit of intervention A is assessed by comparing the combined results from arms 1 (A1 + B1) and 2 (A1 + B2) to the combined results from arms 3 (A2 + B1) and 4 (A1 + B2), with stratification by the level of intervention Fawzi et al. (1999) and Thior et al. (2006) provide examples of factorial designs in mother-to-child HIV prevention trials. To illustrate how investigators might use a factorial design to assess a new microbicide gel, but also to compare two behavioral intervention strategies, suppose subjects are counseled for condom use and other risk- reducing behaviors at one of two levels (e.g., new behavioral risk-reduction intervention versus standard risk-reduction counseling). Then a 2 × 2 facto- rial design aiming to assess the benefits of the microbicide as well as the type of behavioral risk-reduction intervention would have the following arms: Arm 1: Microbicide gel plus standard risk-reduction counseling Arm 2: Microbicide gel plus enhanced behavioral risk-reduction intervention Arm 3: Placebo gel plus standard risk-reduction counseling Arm 4: Placebo gel plus enhanced behavioral risk-reduction intervention This is a partially blinded design because subjects would know if they are receiving an enhanced behavioral risk-reduction intervention versus standard risk-reduction counseling, but they would not know whether they are receiving the microbicide or placebo gel. The assumption of no interac- tion means that the incremental value (e.g., relative risk) of the microbicide relative to placebo is the same for subjects who receive enhanced behavioral risk-reduction intervention versus standard counseling. This is equivalent to saying that the relative benefit of the enhanced behavioral risk-reduction intervention (compared with standard counseling) is the same regardless of whether a subject receives the microbicide or placebo. A quantitative interaction would mean that the direction of the effect of A (or B) is the same regardless of the level of the other factor, but that the effect differs in magnitude. The advantage of a factorial design lies in the fact that if there is no interaction, this design would have about the same power as an equally

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0 ALTERNATIVE DESIGNS sized trial comparing microbicide to placebo in subjects receiving a single type of counseling. Yet this design could assess the added value of the microbicide as well as the difference in effectiveness between the enhanced behavioral risk-reduction intervention and standard counseling. If there is a quantitative interaction, the trial would have about the same power as an equally sized trial comparing microbicide to placebo in subjects receiving a single type of counseling whose effect is, loosely speaking, equal to the average effect of the two types of behavioral risk-reduction interventions in the factorial design. When investigators analyze a factorial trial, the first step is to assess whether the assumption of no interaction or a quantitative interaction is consistent with the data. If it is, then the full data can be used to separately assess each intervention. If there is a qualitative interaction, the levels of each intervention (e.g., A1 versus A2) would be compared separately for the levels (B1 and B2) of the other intervention. As a result, the power to detect differences between the levels of each intervention is reduced because comparisons are based on half the sample size. As noted above, a partially blinded 2 × 2 factorial design that involves a placebo-controlled biomedical intervention and an unblinded comparison of two behavioral interventions may often be expected to have no interac- tion or a quantitative interaction. When a qualitative interaction may still be plausible in such a setting, it may be prudent to size the factorial trial to have reasonable power (e.g., 70 percent) if a qualitative interaction is found. For example, a factorial trial with equal allocation of subjects to each arm, a 5 percent type I error rate, and 90 percent power to detect a reduction in HIV incidence from 3 percent to 1.5 percent would require a total of 4,286 subjects, each followed for 1 year, if there were no interac- tion. If this sample size were increased by 17 percent to 5,036, the power would rise to 94 percent, and the power to test each subgroup separately, assuming a qualitative interaction was found, would be 70 percent. Thus the use of factorial designs with augmented sample sizes offers some protec- tion against an unexpected interaction. Variations on Standard Factorial Design The 2 × 2 factorial design discussed above is intended to provide an example of the potential benefits of a factorial design in a setting where a qualitative interaction is unlikely. The ideas can apply to any two interven- tions that might be used simultaneously, and to two nonzero levels of each intervention, such as two doses or schedules of a microbicide, rather than the presence or absence of the microbicide. In a multisite trial conducted in different sociocultural settings, it may be possible to evaluate multiple behavioral risk-reduction interventions if

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0 METHODOLOGICAL CHALLENGES IN HIV PREVENTION TRIALS an endpoint other than HIV infection could be confidently used to com- pare the behavioral interventions. For example, suppose a trial were being planned to evaluate a new microbicide gel (versus placebo gel) at three sites, and with 1,000 subjects per site. Suppose also that the behavioral interventions could be reliably compared based on reported condom use rather than on the acquisition of HIV. Then, within each site, each of the 1,000 subjects could be randomized to microbicide gel (A1) versus placebo gel (A2), as well as to either intensive or standard counseling. That is, the design would be as follows: Site 1: A1 + S1 vs. A1 + S2 vs. A2 + S1 vs. A2 + S2 Site 2: A1 + S3 vs. A1 + S4 vs. A2 + S3 vs. A2 + S4 Site 3: A1 + S5 vs. A1 + S6 vs. A2 + S5 vs. A2 + S6 Here S1, S3, and S5 refer to the more intensive counseling strategies used at the three sites, while S2, S4, and S6 refer to the standard counsel- ing strategies used at the three sites. With this sample size (250 in each of the four resulting arms), the study may have adequate power to enable investigators to compare different pairs of counseling strategies at each of the three sites if this is based on reported condom use instead of HIV infection rates, while still using all 3,000 subjects to evaluate the efficacy of the microbicide based on HIV infection rates. Investigators would need to carefully examine the details of such designs in specific settings. The key point is that with the use of endpoints other than HIV infection to evaluate the behavioral risk-reduction interventions, it may be possible to tailor behavioral interventions and comparisons to different study sites, and evaluate these in a trial of a biomedical intervention without a substantial increase in sample size or duration. However, when an alternative endpoint cannot be reliably used, the behavioral interventions should be based on the endpoint of HIV infection, which implies that the number of distinct behavioral interventions would typically be the same as the number of biomedical intervention arms. Incomplete Factorial Designs In settings where investigators plan to assess more than one interven- tion, but all combinations of the interventions are not of interest, they can realize economies of scale by using a single trial with a common control group. For example, suppose investigators wish to assess each of two microbicide gels used with either enhanced behavioral risk-reduction inter- vention versus standard risk-reduction counseling. Rather than comparing the gel plus standard risk-reduction counseling to the gel plus the enhanced risk-reduction counseling in one trial, and comparing the gel plus standard

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 ALTERNATIVE DESIGNS risk-reduction counseling with standard counseling in a different trial, the investigators could combine these into a single trial with three arms to reduce the needed sample size, because they could use the same control group (gel plus standard counseling) for both assessments. Such a design can be viewed as an incomplete factorial design because it contains 3 of the 4 possible arms used in the 2 trials. The Breast-feeding, Antiretroviral, and Nutrition (BAN) study now under way in Malawi is using an incomplete factorial design to study the prevention of mother-to-child transmission. In that study, all mothers and infants are given a standard peripartum HIVNET 012 NVP and ZDV/3TC regimens. Mother-infant pairs are randomized to one of three arms: (1) additional maternal-only antiretroviral therapy (ART) versus (2) additional infant-only ART versus (3) no additional infant or mother ART (beyond the NVP and ZDV/3TC standard). Women are also randomized to receive nutritional supplements versus no nutritional supplements.1 The study is an incomplete factorial because the investigators are not evaluating all possible combinations. Recommendation 10-1: Investigators planning late-stage randomized trials of biomedical interventions are encouraged to utilize partially blinded factorial designs in order to also evaluate the relative effective- ness of different behavioral intervention strategies. Factorial designs can provide valuable information about both types of interventions with the same sample size as a trial evaluating only the biomedical intervention. DISCORDANT COUPLE DESIGNS Most late-stage HIV prevention trials of biomedical interventions have used designs which enroll at-risk subjects and follow them for HIV infec- tion, without direct knowledge of their exposures to HIV. An implicit assumption in such studies is that the types and frequencies of HIV expo- sures of participants may vary, but that the randomized intervention groups have similar distributions (“mixes”) of exposures, so that a comparison of the cumulative incidence of HIV infection rates between the intervention arms reflects the relative effectiveness of these interventions in preventing HIV infection. An alternative approach is to conduct what is commonly called a “dis- cordant couples” study, in which HIV-discordant couples are identified and one (typically the uninfected member) is randomized to one of the interven- tion arms. In HIV, discordant-couple designs were initially used to estimate 1 See http://www.id.unc.edu/malawi/studies_research.htm#unccdc.

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 METHODOLOGICAL CHALLENGES IN HIV PREVENTION TRIALS the per-contact transmission risk of HIV. However, they also can be used to evaluate a new intervention. As with traditional designs, the results of such a study can be analyzed by comparing the cumulative incidence rates of HIV infection in the different intervention arms. Despite offering coun- seling on HIV prevention, trials enrolling such couples have recorded HIV infection rates as high as 8–12 per 100 person-years (Quinn et al., 2000; Hugonnet et al., 2002; Allen et al., 2003; Coldiron et al., 2007). However, because more is known about the primary (and sometimes sole) source of exposure of the participants, discordant-couple designs can have several advantages to traditional designs. Efficiency A traditional randomized trial evaluating a new biomedical intervention enrolls subjects who are expected to be exposed to HIV because of their behavior. Given the types and frequency of risky behaviors participants engage in, investigators estimate their potential exposure to HIV. However, some subjects in each study arm will not be exposed to HIV because any risky behaviors they undertake would be with HIV-uninfected people. This would attenuate any effect of the intervention. For others, their HIV expo- sure in each sexual act is not known. For example, a commercial sex worker might be able to convince 75 percent of her partners to use a condom, but investigators do not know how many times those who are HIV infected do or do not use a condom. In contrast, in discordant couples, investigators know the actual HIV exposure of the uninfected partner based on the types and frequency of risky behaviors with the infected partner. (See, for example, Jewell and Shiboski, 1990; Kim and Lagakos, 1990; Jewell and Shiboski, 1992; Magder and Brookmeyer, 1993.) As a result, if the susceptibility of subjects were simi- lar in both types of trials, a study with discordant couples would require a smaller sample size to achieve the same power. Discordant couples could thus be a valuable population for efficacy studies. More Intervention Options Uninfected partners could be randomized to receive an intervention (e.g., a microbicide gel) versus a control (e.g., a placebo gel). Or, the intervention could be directed at the infected partner, to try to reduce the transmissibility of HIV. For example, HPTN 052, a study of 1,750 discor- dant couples, is investigating the efficacy of ART treatment of the infected partner in preventing transmission of HIV to the uninfected partner (www. hptn.org). The Partners in Prevention study is investigating the efficacy of

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 ALTERNATIVE DESIGNS acyclovir suppression of HSV-2 on HIV acquisition in HIV/HSV-2 discor- dant couples (Celum and Wald, 2005). Social Support and Adherence As noted, a trial involving individuals in known discordant couples may enlist both partners in the prevention process rather than just individuals. Such a trial could educate both the infected and uninfected partner on the product regimen, and give both partners social support and HIV prevention tools. In discordant couples in which the woman is HIV-negative, involving both partners in the study can increase the likelihood that they will adhere to condoms, family-planning services, and the study product (Hugonnet et al., 2002; Allen et al., 2003). Scientific Insights Partner studies also facilitate research on other pressing scientific con- cerns, such as the transmission efficiency of certain subtypes of HIV-1, including mutations that confer resistance—a topic of considerable interest in vaccine trials (see, for example, Gilbert, 2001), but also in studies of other biomedical interventions. As the HIV prevention armamentarium expands to include antiretroviral agents such as microbicides and PrEP, involving both partners in clinical trials could advance research on the potential effect of these products on HIV-infected partners. Despite these potential advantages, discordant-couples designs are sometimes not feasible because of challenges in identifying a sufficient number of discordant couples for participation in a trial (Coldiron et al., 2007). In addition, there sometimes are concerns that substantial numbers of couples would break up once they became aware of their discordant status. However, this is not always the case and several studies have not encountered that problem (Allen et al., 2003). With regard to recruitment, the Partners in Prevention Study has successfully enrolled and followed more than 3,000 HIV/HSV discordant couples in an HSV suppression trial in seven countries over a two-year period (Celum, 2007). In endemic areas, such as sub-Saharan Africa, with a high prevalence of HIV infection in both genders, the potential exists to identify discordant couples and enroll the uninfected partner into an HIV prevention trial. Thus, in light of the poten- tial advantages of using discordant couples in late-stage HIV prevention tri- als of biomedical interventions, the committee believes that their feasibility should be assessed in the early stages of the planning of such trials. Recommendation 10-2: When feasible and consistent with the scientific goals of a late-stage HIV prevention trial, investigators are encour-

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 METHODOLOGICAL CHALLENGES IN HIV PREVENTION TRIALS aged to consider discordant couple designs because of their advantages over designs in which the actual HIV exposures of participants are unknown. NONINFERIORITY DESIGNS Padian et al. recently evaluated the use of a diaphragm plus lubricant gel for preventing HIV in a two-arm superiority trial (Padian et al., 2007). The trial randomized sexually active women to the intervention plus coun- seling for condom use versus just counseling for condom use. The treatment arms were unblinded. Overall, the study failed to show that the use of a diaphragm reduced the risk of HIV infection. However, reported condom use was substan- tially lower (54 percent versus 85 percent) in the subjects who received the intervention. Suppose that what actually happened in this trial is that women assigned to the intervention felt that it offered an effective alternative to condoms in protecting against HIV infection, and that they preferred the alternative because they could avoid confrontations with their sexual partners over condom use. In that case, another view of the trial results is that an alter- native strategy to condom use—namely, “use condoms where possible, but if that is inconvenient, use the diaphragm plus lubricant”—may be equally effective in preventing HIV infection as a simple recommendation that women use condoms. However, the former might be preferable because it gives women a choice. Investigators cannot reliably make such an inference based on the simple trial results in Padian et al. (2007), since this is not how the interventions were administered. Nevertheless, the example shows it might sometimes make sense to assess whether one intervention strategy is as good as another, rather than the traditional superiority design in which one seeks to determine whether a particular strategy is superior in efficacy than another. Traditionally, investigators use a noninferiority (sometimes called equivalence) design to compare a new intervention with an established intervention, in settings where the new intervention is expected to have some inherent advantages (such as lower cost or fewer side effects) but similar efficacy. For example, a woman who might find it difficult to con- vince a male partner to use a condom might choose to use a diaphragm. For this woman, a strategy of encouraging her to “use condoms where feasible, but use a diaphragm otherwise” might have equal or better efficacy than a strategy of encouraging only condom use. Yet, even if the efficacy of the first strategy were equal to that of the condom-only strategy, the woman might strongly prefer the diaphragm/condom strategy because it gives her greater control over her HIV infection risk. Here a noninferiority trial

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 ALTERNATIVE DESIGNS might address the scientific goals better than a superiority trial. Noninferi- ority designs have been used in HIV and in a wide variety of other diseases. An early HIV example is a Thai trial (Lallemant et al., 2000) that was initiated after it had been demonstrated in several studies that antepartum/ intrapartum administration of AZT was shown to dramatically reduce mother-to-infant transmission of HIV. Lallemant and colleagues (2000) sought to determine whether a shorter course of AZT could provide similar protective efficacy as the standard course, on the grounds that if it did, it would be less expensive, and perhaps safer, and thus preferable, especially in a resource-limited setting. For a general methodological discussion of noninferiority designs, see D’Agostino et al. (2003). Once initial advances are made for specific types of biomedical inter- ventions for HIV, such as microbicides or PrEP, noninferiority designs might be naturally employed to assess whether a similar preparation or alternative mode of delivery is about as effective as the original, especially if the new product has other advantages, such as lower cost, ease of delivery, or fewer side effects. However, noninferiority designs might also be useful in settings seeking to identify more choices of prevention strategies, and where the specific sci- entific interest is in whether an alternative approach to prevention of HIV transmission is approximately as effective as a more standard approach, in part because of a change in behavior that would be expected to occur with the availability of the new approach, and where the alternative approach may be advantageous in other respects, for example, as in the discussion of the Padian et al. study. Such trials might thus intentionally be unblinded because use of a placebo might not lead to behavior changes typical of what would occur in a real-world setting. CLUSTER RANDOMIZATION This chapter has so far focused on trials in which each individual is randomly assigned to one of the intervention arms. An alternative approach is cluster randomization, in which a group of subjects (e.g., from a specific community) rather than individuals is randomized to each study arm. Clusters can be defined in a number of different ways, depending on the research question. For example, they can be catchment populations at vaccination centers or schools. For a phase 3 microbicide trial, one strategy could be to define clusters as communities served by different health centers, and randomize all the women in a given community to receive either the microbicide gel or the placebo. Investigators have used cluster randomization most often to evaluate interventions normally delivered to groups or communities, such as con- trols on sexually transmitted diseases (Grosskurth et al., 1995; Wawer et

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 METHODOLOGICAL CHALLENGES IN HIV PREVENTION TRIALS al., 1999) or school-based education (Hayes et al., 2005). Some phase 3 vaccine trials have also used the approach (Moulton et al., 2001; Barreto et al., 2002; O’Brien et al., 2003). Investigators prepared for one trial of a pneumococcal vaccine by comparing the advantages of individual and community randomization (Jaffar et al., 1999). In individually randomized trials, subjects from both study arms usu- ally live side by side and receive the intervention and control from the same clinic or other setting. This approach might not resemble what would occur if the intervention were introduced into the community. An advantage of cluster-randomized trials is that they mimic real life more closely, as entire communities receive either the intervention or the control strategy. How- ever, migration can be high in many regions, including areas in Africa, and communities receiving the control strategy would need to provide it to individuals who move into their area from intervention communities, and vice versa. A potential advantage of cluster randomization is that it can allow investigators to estimate individual plus community-level protection against infectious disease. This is known as “herd immunity” (Jaffar et al., 1999). For example, in a trial of a vaccine for pneumonia or malaria, vaccinating all children in a community could reduce exposure by reducing the over- all number of infections in that community. If vaccination leads to herd immunity, a cluster-randomized trial could provide a truer estimate of the effectiveness of the vaccine when used in a normal setting posttrial. In an individually randomized trial, no more than half the target population is usually randomized to the intervention, so vaccinated individuals would be more likely to mix with nonvaccinated individuals, thus increasing their exposure and reducing the possibility of herd immunity. However, herd immunity is unlikely to develop during the relatively short course of a randomized trial. For example, in trials of a vaccine for pneumonia or malaria, the vaccinees—young children—are only a small proportion of the population, and many young children could become infected from adults or children who are not part of the trial. Thus the reduction in exposure that would result from using cluster randomization rather than individual randomization would usually be minimal (Jaffar et al., 1999). Cluster randomization is a natural approach when an intervention includes educational efforts best conducted at the group level. For example, Project Accept (HPTN 043) is the first randomized, controlled phase 3 trial to determine the efficacy of a behavioral/social science intervention with an HIV incidence endpoint in the developing world (NIMH, 2007). The study involves randomizing 34 communities in Africa (in South Africa, Tanzania, and Zimbabwe) and 14 communities in Thailand to receive either commu- nity-based voluntary counseling and testing (VCT) in addition to standard

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 ALTERNATIVE DESIGNS clinic-based VCT, or standard clinic-based VCT alone. The primary objec- tive of this study is to test the hypothesis that communities receiving 3 years of the community-based intervention in addition to the standard services will have lower prevalence of recent HIV-1 infection. Trials involving microbicides and PrEP could be individually or cluster randomized, and in some cases could mix features of each approach. For a trial evaluating a microbicide, with HIV incidence among women as the pri- mary endpoint, a microbicide would need to protect women to reduce HIV infections in men in the community. Reducing the number of HIV-infected men will then reduce the risk to women in the trial and provide an added benefit (herd effect). For a trial of male circumcision, with HIV incidence among men as the primary outcome, a trial would need to protect men to reduce HIV infections in women in the community. Reducing the number of HIV-infected women will then reduce the risk to men in the trial and provide an added benefit. Because trials usually last no more than 2 or 3 years, an appreciable herd effect is unlikely to develop, except in populations where partner change is high, HIV incidence is rising rapidly, and the source of new infec- tions is localized within each community. There are probably relatively few settings where such conditions exist, and even fewer where reliable infor- mation on HIV incidence and the source of infections is well known, or investigators can collect that information quickly and accurately enough to design community-randomized trials of microbicides. A possible exception is polygamous societies where entire households form clusters for random- ization. In general populations, no evidence suggests that providing micro- bicides or PrEP would lead to a herd effect in a cluster-randomized trial. In a partially blinded factorial design aimed at evaluating a new bio- logical intervention as well as comparing two behavioral counseling strate- gies (see Chapter 5), the behavioral component might involve counseling at the group level. In such a setting, concerns about biases that can occur from cluster randomization with a small number of clusters would not generally apply. However, if a “group effect” in behavioral change occurs, investigators might need to make some adjustment to the standard analysis of individual-randomized studies. Further research into the analysis of such mixed designs is warranted. As noted, cluster randomization can be disadvantageous when the number of clusters is too small. Several large cluster-randomized trials have fewer than 10 clusters per arm (Grosskurth et al., 1995; Wawer et al., 1999; Kamali et al., 2003). When there is heterogeneity among the clusters and the number of clusters is not sufficiently large, randomization of the clusters can more easily result in chance differences between those assigned to the different interventions than in individually randomized trials with a similar number of subjects.

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 METHODOLOGICAL CHALLENGES IN HIV PREVENTION TRIALS For example, in the widely cited trial of sexually transmitted disease control in Mwanza, Tanzania (Grosskurth et al., 1995), 12 large communi- ties (i.e., clusters) were randomized to either the intervention or the control. A cohort of 1,000 subjects was evaluated in each community. The baseline HIV prevalence was 3.8 and 4.4 percent, respectively, in the two arms. In a similar-sized cluster-randomized trial of mass syndromic treatment for sexu- ally transmitted diseases in Rakai, Uganda (Wawer et al., 1999), baseline HIV prevalence in the intervention and control arms was 16.1 and 15.5 percent, respectively. Investigators can adjust their estimates of the efficacy of an intervention to help account for such baseline imbalances, but only for known confounders they can measure accurately. Properly designed phase 3 trials that are individually randomized, in contrast, usually have near-perfect control of both known and unknown confounders. For example, in a recent trial of diaphragm and lubricant gel involving just over 5,000 women (Padian et al., 2007)—less than half the number of subjects as in the Mwanza and Rakai trials—baseline indicators such as proportion married, proportion circumcised, and reported condom use were almost identical in the intervention and control arms. The random- ized trials of male circumcision in South Africa, Kenya, and Uganda (Auvert et al., 2005; Bailey et al., 2007; Gray et al., 2007) were of similar size as the trial of diaphragm and lubricant gel (Padian et al., 2007) and also achieved excellent balance between the intervention and control arms. Because of the potential for imbalance between arms in cluster-random- ized trials, investigators should ensure that there are an adequate number of clusters, but also collect data on known potential confounders, so they can also adjust the statistical analysis to account for any differences between arms. This adds complexity to the trial. In a microbicide trial, study staff would need to collect data on all potential risk factors for HIV incidence, such as the frequency and nature of risky sexual behavior. Collecting such data can be a substantial undertaking and require more time from subjects. In contrast, individually randomized trials usually collect minimal data on confounding factors. Cluster-randomized trials may also have less statistical power than individually randomized trials for the same number of individuals. The loss of power can be substantial, depending on the variation in outcomes between clusters, such as HIV incidence. This is known as the “intraclass coefficient of variation” (Guittet et al., 2005). Importantly, power is diffi- cult to estimate accurately before a trial begins, as the intraclass coefficient is not known in advance and is often difficult to estimate. Estimates of the intraclass coefficient in large HIV-prevention trials evaluating controls on sexually transmitted disease have varied widely (Grosskurth et al., 1995; Wawer et al., 1999; Kamali et al., 2003; Todd et al., 2003). Blinding can be essential to an unbiased assessment of a trial’s out-

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 ALTERNATIVE DESIGNS comes. However, blinding might be difficult in community-randomized trials if the product has a major effect on HIV incidence. If HIV incidence drops noticeably in intervention communities and not in control communi- ties, it could become evident which group is receiving the treatment. Overall, cluster randomization has a potentially useful role in HIV prevention studies, especially where some interventions, such as certain counseling or educational interventions, are easier to give to groups rather than individuals. However, such interventions must be used critically to ensure that biases do not result from differences among clusters or a lack of blinding. DYNAMIC DESIGNS More long-term treatments for chronic disease or prevention, as well as a call for more individualized medicine, have spurred growing interest in so-called dynamic intervention strategies. A dynamic regime consists of a sequence of decision rules for how to vary interventions over time according to subject-specific measurements. Although in the early stages of development, dynamic trial designs acknowledge that one intervention may not apply equally well to all people. This is especially true when an inter- vention aims to change behavior (Carroll and Rounsaville, 2007; Dawson et al., 2007). Consider a young woman who has enrolled in an HIV prevention trial. When she begins the study, she requires HIV protection only when her partner, a migrant worker, returns home every three months. The partner does not want to use condoms and would like to have a child. During this time, the woman may prefer a female-controlled product without contra- ceptive properties. In the middle of the study, the partner returns from extended work abroad. This same woman may now require a different form of HIV protection. Her partner may demand sexual intercourse without advance warning and without the use of a condom, making it difficult to use a coitally dependent product. During this time the woman may prefer a daily protection method. By the end of the study, the protective needs of the woman have changed yet again. She is now pregnant and requires a product that will protect her from HIV infection and that is safe to use during pregnancy. Dynamic designs aim to adapt to individuals’ changing needs and opportunities based on predetermined rules. For example, some HIV treat- ment trials prescribe changes in individual treatments when resistance emerges on when his or her viral load is no longer suppressed. HIV preven- tion trials could also offer multiple interventions based on a sequence of predetermined decision rules. To compare two dynamic strategies in a standard parallel design, inves-

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0 METHODOLOGICAL CHALLENGES IN HIV PREVENTION TRIALS tigators would assign one dynamic strategy to one arm and a reference strategy to another. However, to help determine how best to adapt an intervention strategy to become part of a sequence of interventions and responses, sequentially multiple assignment randomized (SMAR) trials have recently been introduced (Murphy, 2005; Murphy et al., 2007). At several stages during such studies, subjects are randomized over a number of pos- sible interventions, which depend on the interventions and responses to that point. In designing sequentially randomized trials or evaluating dynamic intervention strategies, investigators need to consider what observed event might spur a change in intervention, and therefore trigger another randomization. In the context of an HIV prevention trial, at least two types of events might trigger a change in preventive treatment: pregnancy and nonadher- ence to the treatment. As discussed in Chapter 4, despite counseling on use of condoms and providing access to contraceptives, the incidence of pregnancy in many bio- medical HIV prevention trials is very high. Trials typically require women who become pregnant to stop using the product during pregnancy, which can reduce study power. As an alternative to this practice, investigators could accept that women in this age range are likely to become preg- nant, especially when the trial has a long follow-up period, and regard the dynamic intervention as a total package. If the best course of action for pregnant women is unclear, investigators could take the opportunity to learn how best to protect pregnant women from HIV infection, and randomize them at that point over a set of prevention options such as remaining on product versus discontinuing product and initiating intense counseling for ways of preventing HIV infection during pregnancy versus discontinuing product without initiating any additional form of preventive intervention. This approach could yield valuable information for future practice, even if a single trial does not have the power to establish a defini- tive course of action. A dynamic strategy could also be implemented that would give indi- viduals who are poor adherers to the product regimen an alternative pre- vention strategy. For example, investigators could consider at least two different courses of action for participants who cross a predefined adher- ence threshold considered to be unacceptable. First, they could randomize individuals to different interventions to increase it, or second, they could offer the participant an alternative prevention product that is perhaps better suited to the participant. Recommendation 10-3: Investigators should consider the potential merits of using noninferiority, cluster randomization, and dynamic designs in future biomedical HIV prevention trials.

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