Designing & Conducting Trials To Reliably Evaluate HIV Prevention Interventions

Abstract

While much has been achieved, much remains to be accomplished in the science of preventing the spread of HIV infection. Clinical trials that are properly designed, conducted and analyzed are of integral importance in the pursuit of reliable insights about HIV prevention. As we build on previous scientific breakthroughs, there will be an increasing need for clinical trials to be designed to efficiently achieve insights without compromising their reliability and generalizability. Key design features should continue to include: 1) the use of randomization and evidence-based controls, 2) specifying the use of intention-to-treat analyses to preserve the integrity of randomization and to increase interpretability of results, 3) obtaining direct assessments of effects on clinical endpoints such as the risk of HIV infection, 4) using either superiority designs or non-inferiority designs with rigorous non-inferiority margins, and 5) enhancing generalizability through the choice of a relative risk rather than risk difference metric. When interventions have complementary and potentially synergistic effects, factorial designs should be considered to increase efficiency as well as to obtain clinically important insights about interaction and the contribution of component interventions to the efficacy and safety of combination regimens. Key trial conduct issues include timely enrollment of participants at high HIV risk recruited from populations with high viral burden, obtaining ‘best real-world achievable’ levels of adherence to the interventions being assessed and ensuring high levels of retention. High quality of trial conduct occurs through active rather than passive monitoring, using pre-specified targeted levels of performance with defined methods to achieve those targets. During trial conduct, active monitoring of the performance standards not only holds the trial leaders accountable but also can assist in the development and implementation of creative alternative approaches to increase the quality of trial conduct. Designing, conducting and analyzing HIV prevention trials with the quality needed to obtain reliable insights is an ethical as well as scientific imperative.

1. Introduction

During the past quarter century, much has been achieved in evaluating interventions for preventing the spread of HIV infection. Initial breakthroughs were obtained in the setting of mother-to-child transmission, with the establishment of efficacy of AZT in developed country settings (ACTG 076 trial¹) and of nevirapine in developing country settings (HIVNET 012²). Later, antibiotics were evaluated in HPTN 024³, while behavioral interventions and community mobilization were assessed in HIVNET 015 and HPTN 043^4-5. Three trials of medical male circumcision firmly established the efficacy of circumcision in reducing risk of HIV acquisition in men^6–8. The CAPRISA 004, HPTN 035, RING and MTN 020 trials provided insights about microbicides and the vaginal ring^9–12 and many informative vaccine trials have been conducted, including RV144, STEP, PHAMBILI, HVTN 505 and VAXGEN^13–18. Use of anti-retrovirals have provided significant breakthroughs, including strategies based on treating the infected participant (HPTN 052¹⁹), and based on pre-exposure prophylaxis (PrEP) for the uninfected partner, both in heterosexual exposure (Partners PrEP, CDC TDF2, FemPrEP and VOICE^20–23) and in MSMs (iPrEx, PROUD, and iPERGAY^24–26). The ECHO trial²⁷ has evaluated the relative influence of contraceptive strategies on HIV risks, while the HPTN 071 PopART trial²⁸ is providing important insights about combination interventions.

Even with these achievements, much remains to be accomplished in the science of preventing the spread of HIV infection. As we build on previous scientific advances, there will be an increasing need for clinical trials to have designs providing enhanced efficiency. Current generation PrEP trials, based on long acting anti-retrovirals in MSMs (HPTN 083) and in women (HPTN 084), have designs involving approximately 10,000 person-years of follow-up^29–30, while ongoing trials evaluating vaccines and monoclonal antibodies (HVTN 702, HVTN 703/HPTN 081, HVTN 704/HPTN 085 and HVTN 705) also have substantial size^31–34. Future generation trials may need to be even larger in order to reliably address effects on HIV transmission.

The design, conduct and analysis of future trials not only should achieve efficiency, but also should ensure the achievement of reliable and generalizable insights about HIV prevention. We will discuss the importance of several design features, including the use of randomization and evidence-based controls, use of intention-to-treat analyses to preserve the integrity of randomization and increase interpretability of results, the need for direct assessments of effects on clinical endpoints such as the risk of HIV infection, and the use of non-inferiority designs having rigorous non-inferiority margins and enhanced generalizability through the choice of a relative risk rather than risk difference metric. We will discuss the role of factorial designs when interventions have complementary and potentially synergistic effects. Key trial conduct issues also will be considered, including the importance of achieving timely enrollment of participants at high HIV risk from populations having high viral burden, obtaining ‘best real-world achievable’ levels of adherence to the interventions being assessed and ensuring high levels of retention.

2. Trial Design Considerations

Ensuring clinical trials are properly designed is of integral importance to obtaining reliable insights about interventions to prevent acquisition of HIV.

2.1. Randomization, evidence-based controls, and ‘feels, functions, survives’ measures

As recently indicated, “Medical interventions must be evaluated in a manner that is ethically acceptable…Ethical considerations relate to safeguarding the interests of study participants, and to achieving timely and reliable insights about interventions to enhance the health of the public.”³⁵ Therefore, implementing efficient and reliable clinical research approaches is not only a scientific but also an ethical imperative. It also was noted that “The goal of clinical research is not simply to provide those pursuing safe and effective interventions a “choice,” but rather an “informed choice”.” Hence, as we pursue greater efficiency, to be admissible, a design must also ensure that the trial provides sufficiently reliable insights about efficacy and safety that the public is properly informed in decision-making regarding its use.

Since most advances in the prevention of irreversible morbidity/mortality outcomes are moderate in size, randomization usually is of integral importance to being able to reliably discern effects of the intervention from the influence of baseline prognostic factors, such as characteristics of the participant or disease process³⁵. Interpretability and efficiency are further enhanced by the use of control regimens that are typically high-quality versions of standard-of-care in the setting in which the trial is being conducted, to satisfy distributive justice considerations, and that include components that have been established to have favorable benefit-to-risk profiles.

The choice of the primary outcome measure also is of integral importance to scientific integrity. The interpretability and reliability of trial results are enhanced by using outcomes that are direct measures of tangible outcomes for participants, such as how they ‘feel’, (for example, their symptoms), how they ‘function’, (for example, their activities of normal daily living), or how long they ‘survive’. In HIV clinical trials, among the direct measures of tangible outcomes are ‘progression to major symptoms’, ‘acquisition of HIV infection’ or death. Replacement endpoints often are considered in order to reduce the size and duration of a clinical trial. These could include ‘self-reported risk behavior’ in the trial of a behavioral intervention, immunological biomarkers for a vaccine, or levels of adherence for a PrEP intervention. While these replacement endpoints may be correlated with ‘feels, functions, survives’ endpoints, it is important to recognize that “a correlate does not a surrogate make.”^36–37 As noted in Figure 1a, a cell-mediated or humoral immune response achieved by a vaccine could overestimate effects, especially when it is unknown what magnitude, breadth and duration of effects would be needed for protection; in Figure 1b, the vaccine’s effectiveness in a population, mediated through effects on infectiousness and disease progression in addition to effects on susceptibility, could be underestimated by simply assessing effects on HIV acquisition. Replacement endpoints, while sensitive to the intended effects of an intervention, often yield unreliable results due to their insensitivity to off-target effects. In Figure 2, a trial comparing a vaginal microbicide with a placebo-gel control could underestimate efficacy since the control arm carries the lubrication and physical barrier effects of the microbicide, but also could overestimate effectiveness due to off-target effects such as reduced condom use. For this reason, establishing ‘super-superiority’ often would be needed to ensure an HIV prevention intervention has a favorable impact on effectiveness. In most HIV prevention trials settings, reliability is best achieved through the use of outcomes such as ‘HIV infection’, while biomarkers or other replacement endpoints should be supportive measures. Such an approach also provides evidence needed in the future to validate the reliability of replacement endpoints.³⁸ For example, the availability of such evidence enabled a rigorous justification for the use of ‘durable undetectable levels of HIV’ as a replacement endpoint in the HIV treatment setting.

Figure 1:

A vaccine’s effect on a replacement endpoint (i.e., ‘targeted immune response’ or ‘susceptibility’) could provide false positive (in A) or false negative (in B) conclusions about a vaccine’s effect on a ‘feels, functions or survives’ or ‘symptomatic disease/death’ endpoint if its effect on the (solid line) pathway mediated through the replacement endpoint is meaningfully offset by the influence of other (dotted line) causal pathways.

Figure 2:

A vaginal microbicide’s effect on HIV infection in a placebo-controlled trial could underestimate its real-world effectiveness in preventing HIV infection if the placebo gel is not inert (due to its lubrication or physical barrier effects) and could overestimate real-world effectiveness due to the presence of disinhibition.

2.2. Non-inferiority trials with rigorous non-inferiority margins

As discussed in the Introduction, multiple trials have been completed evaluating the efficacy of daily oral tenofovir/emtricitabine (TDF/FTC) as PrEP in several settings^20–26. Results have been promising, yet there have been obvious inconsistencies across trials in the estimated effects on risk of HIV infection, especially in women.³⁹ These inconsistences appear to be related to each trial’s average level of adherence. Hence, there is considerable interest in pursuing an alternative approach based on use of long acting cabotegravir injectable (CAB-LA). While CAB-LA could provide improved protection, it would be an attractive alternative option to TDF/FTC (in settings where TDF/FTC is meaningfully effective) even if effects of both regimens on risk of HIV infection were truly similar. This is due to TDF/FTC’s integral role in first line treatment for HIV infected patients and, thus, the importance of reducing the risk of the development of resistance that could occur from its use as PrEP.

These considerations provide classic motivation for using a non-inferiority trial design to evaluate CAB-LA, especially in the MSM setting where there is stronger evidence regarding the favorable effects of TDF/FTC. HPTN 083 is such a trial, designed to determine whether the efficacy of CAB-LA is either superior or ‘similar’ to that of the active comparator, TDF/FTC, in the MSM setting. ‘Similarity’ would be established formally by ruling out that the relative risk for HIV infection is not unacceptably worse on CAB-LA relative to TDF/FTC; i.e., ruling out a pre-specified non-inferiority margin, M.

The choice of M often is controversial. If the HPTN 083 non-inferiority trial were to be conducted in a high risk setting with sufficient duration of follow-up that the TDF/FTC controls would have 40 HIV infections per 1000 participants, then only 88 HIV infection events would be needed to have 90% power to rule out a M = 1.5 non-inferiority relative risk margin, (i.e, that CAB-LA would have 60 HIV infections per 1000 participants), with traditional 2.5% false positive error rate under the alternative hypothesis that CAB-LA has a 25% relative reduction in risk (i.e, that CAB-LA would have 30 HIV infections per 1000 participants). However, using such a large non-inferiority margin would require justification that it would be clinically acceptable to allow up to 20 additional HIV infections per 1000 participants. If it were argued that no more than 5 additional HIV infections per 1000 participants would be acceptable, (even with the importance of preventing development of resistance to an intervention that is of integral importance in the HIV treatment setting), then the margin would be M = 1.125 and the corresponding number of HIV infection events in the trial would need to be 256.

While there is legitimate interest in reducing the size of non-inferiority trials, (usually achieved by choosing larger non-inferiority margins), it would be a serious issue if a standard-of-care active comparator regimen, established to provide clinically meaningful protection, were to be replaced by a meaningfully less effective intervention. Therefore, it is important to develop and implement rigorous evidence-based non-inferiority margins.

To justify a ‘large’ non-inferiority margin, the active comparator regimen needs to have clinical efficacy that is of a substantial magnitude and is precisely estimated. Because the effect of the active comparator in the setting of the non-inferiority trial is approximated by its estimated effect in previous controlled trials, it also is important that these estimates from other trials truly can be generalized to the setting in which the non-inferiority trial is being conducted.^40–42 That latter requirement is referred to as the ‘constancy assumption’. However, the constancy assumption could be invalid if there are factors that influence the size of effect of the active comparator and that are distributed differently between those previous trials and the non-inferiority trial; these factors could be baseline characteristics, levels of use of supportive care, differences in the dose, schedule or level of adherence to the active comparator, or differences in the efficacy endpoints.

The derivation of the non-inferiority margin, M, is illustrated using the setting of the HPTN 083 trial, (see Figure 3). Based on an aggregation of evidence from placebo-controlled superiority trials, iPrEx, PROUD and iPERGAY^24–26, the placebo would have an estimated 2.20-fold higher risk of HIV infection relative to TDF/FTC. Given uncertainty about the validity of the constancy assumption then, by convention, the lower limit of the 95% confidence interval for the placebo to TDF/FTC relative risk obtained from the aggregation of evidence from these three trials, (i.e., 1.52), is used as the estimate for the Placebo to TDF/FTC relative risk in the HPTN 083 trial. Since it is important to preserve at least 50% of the effect of the active comparator, the non-inferiority margin, M, is chosen to be 1.23 (which is the square root of 1.52).

Figure 3:

The confidence interval (dotted line) for the hazard ratio for HIV infection on the experimental regimen, CAB-LA, relative to the active control, TDF/FTC, should rule out the non-inferiority margin, 1.23; the derivation of this margin adjusts for uncertainty about the validity of the ‘constancy assumption’ by presuming that Placebo resides at the lower limit of the confidence interval (solid line) for the Placebo to TDF/FTC hazard ratio that is estimated from previous trials, (yielding 1.52), and then by preserving ≥ 50% of the effect of the active comparator on the log scale of the analysis, (i.e. by taking the square root of 1.52).

As recently indicated, “Non-inferiority trials with non-rigorous margins allow substantial risk for accepting inadequately effective experimental regimens, leading to the risk of erosion in quality of health care…”⁴⁰. Hence, evidence-based non-inferiority margins should be formulated using adjustments accounting for the unreliability arising from inherent uncertainty about the validity of the constancy assumption, and should be formulated to preserve an appropriate percentage of the effect of the active comparator.

2.3. Generalizability using absolute difference metrics vs. relative risk metrics

In non-inferiority trials evaluating the efficacy of antibiotics in the setting of severe pneumonia, the relative merits of analyses based on absolute differences in risk versus relative risks have been debated. In such trials currently conducted in the setting of serious (e.g., ventilator-associated) pneumonia where mortality on active comparator antibiotics could be 20–25%, there is agreement due to the clinical relevance of increases in mortality that a non-inferiority margin, M, could be no higher than 10% when using the absolute difference metric, which corresponds in that setting to a margin of 1.67 when using an odds ratio metric. Based on this context, an issue of central importance is whether there is sufficient evidence about the effect of active comparator antibiotics, when using methods discussed in the previous sub-section, to justify using margins of that magnitude.

Of particular concern in these non-inferiority trials is the validity and generalizability when a substantial number of lower risk participants would be enrolled. Table 1 provides substantive evidence that the relative risk metric provides enhanced generalizability in that setting.⁴² In each of the six cells created by combinations of three subgroups by age and two by bacteremia status, it is apparent that antibiotics broadly have important beneficial effects on mortality when compared with ‘no specific treatment’. When using the absolute difference metric, a non-inferiority margin M =10% could be justified when patients are either bacteremic or older. However, such a large margin would be not be justified in non-bacteremic younger patients, having much lower mortality even when receiving ‘no-specific treatment’. In contrast, when using a relative risk metric, a non-inferiority margin of approximately 1.67 would be valid in all subgroups of patients. (Even in the younger bacteremic participants, where the odds ratio-based margin is only 1.41 due to the small number of patients receiving antibiotics, the evidence would justify using a margin of 1.64 when one conservatively compares the 126 younger patients receiving no specific treatment with the pooled 102 bacteremic patients under the age of 50 who received antibiotics.)

Table 1:

The mortality rate (deaths divided by number of patients) is provided in patients with severe pneumonia, when receiving either ‘no specific treatment’ or treatment with antibiotics (i.e., penicillin or sulfonamides), and is presented by age and by bacteremia status⁴². In each of the six cells, the estimated absolute difference, with 95% confidence interval, is presented along with a margin, M, that would preserve at least 50% of treatment effect, when using the absolute difference metric (ADM) or the odds ratio metric (ORM). (Data obtained from Fleming TR, Powers JH. Clin Infectious Diseases 2008; 47: S108–20).

By Age	Bacteremic Patients No Specific Treatment   Antibiotics	Non-Bacteremic Patients No Specific Treatment  Antibiotics
<30 #Deaths/#Patients	81 / 126 5 / 21   64.3%   23.8%	90 / 1036 25 / 1044   8.69%    2.39%
Absolute Difference; (C.I.) M Preserving 50% effect	40% (20%, 60%) ADM: 10% ORM: 1.41	6.3% (4.3%, 8.2%) ADM: 2.2% ORM: 1.57
30–49 #Deaths/#Patients	319 / 428 23 / 81   74.5%   28.4%	218 / 1222 125 / 1634   17.84%   7.65%
Absolute Difference; (C.I.) M Preserving 50% effect	46% (35%, 57%) ADM: 18% ORM: 2.08	10.2% (7.7%, 12.7%) ADM: 3.8% ORM: 1.44
≥50 #Deaths/#Patients	368 / 395 40 / 84   93.2%    47.6%	353 / 715 23 / 143   49.4%    16.1%
Absolute Difference; (C.I.) M Preserving 50% effect	46% (35%, 57%) ADM: 17% ORM: 2.90	33% (26%, 40%) ADM: 13% ORM: 1.78

Extensive evidence from the setting of antibiotics to reduce mortality in serious pneumonia indicates a tendency for enhanced validity and generalizability when using a relative risk metric to derive the non-inferiority margin, since inferences would remain valid even if the trial were to enroll a substantial number of younger non-bacteremic participants. Furthermore, for both non-inferiority and superiority trials that use a relative risk metric, results from trials conducted in higher risk participants can more readily be generalized to those with lower risk. Among the important benefits of this generalizability is the motivation it provides sponsors to enroll higher risk participants into their trials, since the power of a trial using relative risk metrics (whether it be an odds ratio or a hazard ratio) is essentially a function of the number of events. This encourages obtaining direct assessments of benefits and risks in clinical settings where the unmet need tends to be greatest. Importantly, even when the relative risk metric is used for the primary analysis of data, results still can be presented descriptively using the risk difference metric.

2.4. Factorial designs: combination regimens with complementary mechanisms

In HIV treatment settings, the most significant breakthroughs occurred with use of combination anti-retrovirals. It is plausible that effects of interventions for prevention of HIV also could be positively synergistic. For example, it is likely that the public health effectiveness of a treatment-as-prevention intervention would be enhanced by interventions to increase HIV testing and linkage-to-care.

If experimental interventions have complementary mechanisms of action and could be delivered simultaneously, evaluating their effects in a factorial design should be considered. Recent research exploring multiple trial designs that could be applied in an HIV prevention setting revealed that factorial designs yield increases in efficiency in a wide array of settings.⁴³

As an illustration, in a setting where treatment as prevention would be provided to all HIV-positive individuals and condom use would be strongly promoted, HIV-negative participants could be randomized between PrEP regimens (as the first factor), a vaccine vs. a monoclonal antibody vs placebo (as the second factor), and self-testing HIV kits vs. testing at the clinic every three months (as the third factor). This would be conceptually similar to the factorial designs used in the Women’s Health Initiative⁴⁴, where participants were randomized to vitamins (yes vs no), hormone supplementation (yes vs no) and exercise (yes vs no). While each participant would be encouraged to engage in all randomizations, a partial factorial design could be used as in the Women’s Health Initiative where each participant would be allowed to decide whether to participate in one, two or all three of these randomizations.

In addition to providing increases in efficiency, the factorial design has additional important scientific advantages. It would provide direct insights (albeit not definitive evidence) about whether there is an interaction between interventions, (i.e., a positive or negative synergy). This is of clinical importance in guiding decisions about whether to make simultaneous use of two or more interventions. Further, when a prevention strategy based on combination interventions is used, if that strategy is effective, the factorial design provides direct insights of considerable clinical and regulatory importance about the contributing positive or negative effects of individual components.

2.5. Approaches for targeting high risk cohorts

Identifying populations at high risk of HIV infection for recruitment into HIV prevention trials is essential to reduce trial duration and to direct research efforts to those most in need. Standard approaches for doing so make use of traditional surveillance data; for example, data from Botswana antenatal clinics provide trends in prevalence over time among different age groups and locations⁴⁵. But the usefulness of such information might be enhanced if combined with information regarding features of contact networks through which HIV spreads. While the potential for such benefits may be large in theory, the degree to which they can be realized in practice depends on resolving important issues relevant to combining and analyzing data from different sources--especially regarding privacy and confidentiality⁴⁶. One important source of network-level information is HIV viral sequences whose analyses can provide information regarding transmission dynamics^47–48; such information is important for development of appropriate agent-based models for predicting HIV risk among different subpopulations. In fact, targeting members of rapidly growing HIV clusters (defined by viral genotype) and their contacts is now under consideration by health departments as a potentially useful HIV control strategy⁴⁹; this may also be a fruitful way to recruit high-risk participants to HIV prevention studies. There are two ways in which such an approach might be used: 1) by identifying high risk subjects themselves—e.g. HIV- contacts of members of such clusters, and 2) by identifying people who share demographic, behavioral, or other characteristics with cluster members and contacts. The former may be more direct and therefore more likely to target high risk participants, but may be too labor intensive to be practical; the latter would be easier to implement but its value in identifying high risk subjects remains to be established. For either approach, databases in which routinely collected viral genetic sequences are linked to patient-level data would be required. Such linkage already exists in databases developed by the treatment-as-prevention trials sponsored by the Office of the Global AIDS Coordinator. In addition, these studies made use of extensive epidemic modeling during their design phase and are currently conducting viral genetic linkage analysis. Hence communities that participated in treatment-as-prevention studies might provide excellent settings for designing efficient cluster-randomized trials—in which the impact of interventions on HIV incidence reflects both direct and indirect effects—but would also be of value in trials that randomize participants at the individual level. In fact, the second phase of the SEARCH study-a cluster-randomized treatment-as-prevention study underway in Kenya and Uganda--will “quantify the health, economic and educational impact of targeted Pre-Exposure Prophylaxis (PrEP), targeted HIV testing and targeted care interventions in the context of universal treatment and streamlined care.”⁵⁰ Data from these and other ongoing trials, as well as simulation studies based on data from completed trials, will provide a basis for investigating the extent to which novel methods of identifying high risk subjects can reduce duration and cost of HIV prevention research studies.

3. Trial Conduct and Analysis Considerations

Ensuring clinical trials are properly conducted is of integral importance to obtaining reliable insights. To enable the trial to provide timely results with the targeted level of precision, an adequate number of sites should be engaged to enable enrollment to be completed within the projected time frame, and these participants should be at high HIV risk, recruited from populations having high viral burden. Participants also should have ‘best real-world achievable’ levels of adherence to the randomized interventions, as well as high levels of retention. To conduct trials in a high-quality manner with respect to each of these issues, we need active rather than passive approaches. First, performance standards should be pre-specified that are adequately stringent to ensure reliability of results; second, approaches should be pre-specified that would be anticipated to be adequate to achieve these performance standards; and third, there should be ongoing oversight by the trial’s sponsor and by independent experts (such as the Data Monitoring Committee) to hold accountable those conducting the trial; if the performance standards are not being met, then creative approaches to achieve improved performance should be identified and implemented. For example, if early evidence from the trial indicates the rate of HIV infection is considerably lower than assumed at trial design, then support should be given to existing sites to assist in enrolling higher risk participants, and enrollment could be redirected to existing or new sites with access to populations with higher viral burden.

Pre-specifying proper methods of analysis also is of integral importance. To preserve the integrity of randomization and to enhance interpretability of results, intention-to-treat (ITT) analyses usually should be the pre-specified primary method of analysis. For example, if women non-adherent to the microbicide regimen to which they are randomized were to be excluded from the analysis, the integrity of randomization would be compromised if such women tend to have higher risk behaviors, or if such women had experienced off-target effects of the intervention, such as epithelial disruption. As recently indicated, “In order to preserve the integrity of randomization, all patients should be followed until the complete capture of trial outcomes, even after patients have discontinued randomized treatment or initiated other interventions.”⁵¹

4. Conclusions

Achieving proper design, conduct and analysis of clinical trials is of integral importance in the pursuit of reliable insights about HIV prevention. Numerous trials, including those discussed in the Introduction, have provided significant enlightenment, not only about the efficacy and safety of interventions to prevent the spread of HIV, but also about the value of scientific rigor: the importance of randomization, having evidence-based controls, use of intention-to-treat analyses, use of clinical endpoints such as HIV infection that enable direct assessments of ‘feels, functions, survives’ effects of interventions, and being properly powered for superiority or to rule out rigorous non-inferiority margins. These previous trials also have demonstrated the value of high quality of trial conduct: using active rather than passive approaches to achieve timely enrollment of participants at high HIV risk from populations having high viral burden, potentially identified with the assistance of creative mathematical modeling, and to obtain ‘best real-world achievable’ levels of adherence to the interventions being assessed and high levels of retention.

As we build on previous scientific breakthroughs, lower rates of HIV infection will lead to an increasing need for clinical trials to be designed to be as efficient as possible; however, this does not mean that we should abandon those principles regarding design, conduct and analysis that have been integral to the remarkable achievements in HIV prevention research during the past quarter century. Calculations in Table 2 reveal that, even if current generation PrEP trials yield positive results, the next generation of trials might require only modestly larger sample sizes than the current trials, especially if there is an expectation of meaningful further reductions in HIV infection rate with use of these future interventions. Creative approaches such as factorial designs should be considered when experimental interventions have complementary and potentially synergistic effects, not only to increase efficiency, but also to provide clinically important insights about interactions between component interventions of the combination regimen and about the contribution of each of these component interventions to the efficacy and safety.

Table 2:

Key trial design features are provided for pre-exposure prophylaxis (PrEP) HPTN 083 & HPTN 084 trials, evaluating the effects on HIV infection of the injectable long acting cabotegravir regimen (CAB-LA) relative to the TDF/FTC active control regimen. In these trials, the TDF/FTC control regimens are expected to have annual HIV incidence rates of 2.09% and 2.07%, respectively; by these derivations (shown in darker black), the experimental arms would yield statistically favorable results with estimated annual HIV incidence rates of 1.90% and 1.43%, respectively. Hence, even if these current generation trials are positive, if future interventions are expected to be meaningfully more effective than standard-of-care, the next generation trials could be conducted with achievable sample sizes, (i.e., 5000 participants). ‘MSM’: men who have sex with men; ‘TGW’: transgender women; ‘W’: women; ‘M’: men; ‘PY’: person years

	HPTN 083 CAB-LA vs TDF/FTC			HPTN 084 CAB-LA vs. TDF/FTC
Population (Hi Risk)	MSM & TGW			W sex with M
Background Incidence	4.0/100 PY			3.5/ 100 PY
Efficacy @ 100% adher	83%	83%		85%	85%
Adherence	73	57.5		80	48
Incidence (#/100 PY)	1.56 vs. 2.09			1.12 vs. 2.07
Hazard ratio of alternative	0.75		Stat Sign if estimated HR = 0.91.....0.69	0.54
Hazard Ratio under Null	1.23			1.00
Required # of Events	172		CAB-LA incidence 1.90.....1.43	112
(False-positive error rate: 0.025; 90% statistical power)
Total sample size	4500		5000	3200
Duration of follow-up	125 wks (65–185)			133 wks (81–185)

Designing and conducting HIV prevention trials to obtain insights in a manner that not only is timely and efficient, but also achieves reliability and generalizability, is an ethical as well as scientific imperative.