Study to Evaluate the Safety and Efficacy of Emtricitabine and Tenofovir Alafenamide (F/TAF) Fixed-Dose Combination Once Daily for Pre-Exposure Prophylaxis in Men and Transgender Women Who Have Sex With Men and Are At Risk of HIV-1 Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate the Safety and Efficacy of Emtricitabine and Tenofovir Alafenamide (F/TAF) Fixed-Dose Combination Once Daily for Pre-Exposure Prophylaxis in Men and Transgender Women Who Have Sex With Men and Are At Risk of HIV-1 Infection (NCT02842086), a randomized phase 3 study. The primary outcome is Incidence of HIV-1 Infection Per 100 Person Years (PY).

2. Clinical Question

The study was designed to assess HIV-1 infection rates in the two groups, with a minimum follow-up of 48 weeks and a requirement that at least 50% of participants complete 96 weeks of follow-up after randomization. The primary endpoint was an incidence rate rather than simply the proportion of participants who became infected. This approach relates the number of infections to the accumulated time participants were followed while at risk.

The registry record describes a randomized, double-blind, parallel-group Phase 3 study. It lists an enrollment of 5399 and identifies HIV-1 pre-exposure prophylaxis as the condition under study. The primary analysis used the Full Analysis Set, defined by randomization, receipt of at least 1 dose, HIV-negative status on Day 1, and at least 1 postbaseline HIV laboratory assessment. That definition clarifies who contributed to the primary analysis, but does not by itself establish that every enrolled participant contributed data to it.

The question concerns the comparative infection rates recorded during this study. It does not, on its own, establish the practical importance of a difference, address every potential outcome, or tell readers how the study’s results apply to people outside the registry’s stated population.

3. Trial Design

This was a Phase 3 randomized, double-blind, parallel-group study sponsored by Gilead Sciences. Participants were assigned to daily F/TAF or daily F/TDF for HIV-1 pre-exposure prophylaxis. During the blinded phase, the F/TAF group received F/TAF with F/TDF placebo, while the F/TDF group received F/TDF with F/TAF placebo. The registry lists an enrollment of 5399.

The study’s primary objective was to assess HIV-1 infection rates. The stated primary assessment period was when all participants had completed a minimum follow-up of 48 weeks and at least 50% had completed 96 weeks after randomization or had permanently discontinued from the study. The timeframe also specifies a maximum of 125 weeks. The registry describes this follow-up rule, but does not report the actual follow-up distribution for the primary analysis.

The record describes additional treatment phases. Once all participants had been on blinded treatment for at least 96 weeks, the study was to be unblinded and participants offered the option to continue with open-label F/TAF for 96 weeks. Participants remaining at Open-label Week 96 could opt to continue open-label F/TAF in an extension phase for 408 weeks. These are descriptions of the planned options; the record does not establish how many participants entered or completed those phases.

The study status is listed as terminated. The registry record does not report the reason for termination. It also does not report the trial’s original sample-size justification, the allocation ratio used in the trial’s design, an interim-analysis plan, or a complete statistical-analysis plan. Those details cannot be inferred from the planning illustrations or from the posted outcome estimates.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 5857 participants were screened.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set included all participants who were randomized into the study, received at least 1 dose of study drug, were not HIV positive on Day 1, and had at least 1 postbaseline HIV laboratory assessment.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: The Safety Analysis Set included participants who were randomized and received at least 1 dose of study drug. Participants were grouped according to the treatment they actually received.

6. Primary Endpoint

The registry lists the primary outcome as Incidence of HIV-1 Infection Per 100 Person Years (PY), measured over When all participants completed minimum follow-up of 48 weeks and at least 50% of the participants completed 96 weeks of follow-up after randomization or permanently discontinued from the study (maximum 125 weeks).

The primary endpoint is the incidence of HIV-1 infection per 100 person-years. The registry defines the rate as the number of participants who became HIV infected after the first dose, divided by the sum of participant-years of follow-up while participants were at risk. In this definition, a year is 365.25 days. The person-time denominator matters because participants may contribute different amounts of at-risk follow-up.

HIV-1 infection was defined using one or more specified laboratory criteria. These include serologic evidence of seroconversion, virologic evidence from a positive qualitative HIV-1 RNA test or detectable quantitative HIV-1 RNA test, or evidence of acute HIV-1 infection based on p24 antigen or RNA findings in the absence of reactive HIV-1 antibody results. The record also states that central-laboratory or local-laboratory HIV tests could contribute to the definition, and that serologic evidence excluded HIV-vaccinated participants.

An incidence rate is useful when the amount of time at risk differs across participants or groups. It expresses infections relative to accumulated exposure time, rather than treating every participant’s follow-up as identical. It does not communicate the same quantity as a risk over a fixed period, and it should be interpreted in light of the study’s follow-up and infection definitions.

The registry reports the primary rate for each group with a 95% confidence interval. The rate ratio compares the groups’ rates, while the confidence interval conveys uncertainty around that comparison. Neither the rate nor its interval alone describes all aspects of safety, adherence, or outcomes beyond the recorded assessment period.

7. Results Posted in the Registry

• Truvada (TVD): 0.34 versus 0.16 (HIV-1 infections per 100 PY) on control; rate ratio 2.14 (95% CI 0.80–5.71, derived from the posted confidence limits); p ≈ 0.130.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percent Change From Baseline in Hip Bone Mineral Density (BMD) at Week 48 in the Blinded Phase

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Truvada (TVD): mean -0.97 versus 0.22 on control; difference -1.19 (95% CI -1.72 to -0.66), standardized effect d = -0.49; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Truvada (TVD) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percent Change From Baseline in Spine BMD at Week 48 in the Blinded Phase

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Truvada (TVD): mean -1.06 versus 0.51 on control; difference -1.57 (95% CI -2.22 to -0.92), standardized effect d = -0.53; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Truvada (TVD) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Serum Creatinine at Week 48 in the Blinded Phase

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Truvada (TVD): mean 0.01 versus -0.01 on control; difference 0.02 (95% CI 0.01 to 0.03), standardized effect d = 0.18; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Truvada (TVD) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover several domains rather than a single underlying construct. They include hip and spine bone mineral density, urine markers, urine protein categories, serum creatinine, and another HIV-1 infection incidence measure. The posted numerical results include Week 48 bone mineral density and serum creatinine comparisons. These endpoints provide additional descriptive and comparative information alongside the primary infection-rate outcome.

Across the posted continuous comparisons, the arm-level summaries show more favorable changes for the Descovy group than the Truvada group for hip and spine bone mineral density, while the serum creatinine change is lower for Descovy than for Truvada. The registry also reports sponsor analyses for these outcomes. These secondary patterns concern laboratory or body-composition measures, not the primary question of HIV-1 infection incidence, and they do not change the primary rate-ratio estimate.

Secondary outcomes can help describe a broader profile of observed results, but they generally carry less inferential weight than a pre-specified primary endpoint. Multiple outcomes create multiple opportunities for apparently notable results. Unless multiplicity is addressed through an appropriate pre-specified strategy, unadjusted p-values may overstate how strongly the full set of results supports a finding. The multiplicity plan is not reported in the registry record.

The registry lists 16 outcome measures and 14 analyses, and 15 secondary outcomes are posted. Those counts describe the record’s outcome and analysis listings; they do not establish which outcomes were prioritized in the original statistical plan or how unreported outcomes were handled. The registry record does not provide enough information to assess the full analysis hierarchy, multiplicity adjustment, or missing-data methods across the secondary endpoints. Accordingly, secondary results are best read as supporting context rather than as substitutes for the primary endpoint.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Percent Change From Baseline in Hip Bone Mineral Density (BMD) at Week 48 in the Blinded Phase
• Percent Change From Baseline in Spine BMD at Week 48 in the Blinded Phase
• Percent Change From Baseline in Urine Beta-2-Microglobulin to Creatinine Ratio at Week 48 in the Blinded Phase
• Percent Change From Baseline in Urine Retinol Binding Protein (RBP) to Creatinine Ratio at Week 48 in the Blinded Phase
• Number of Participants by Urine Protein (UP) and Urine Protein to Creatinine Ratio (UPCR) Categories at Week 48 in the Blinded Phase
• Change From Baseline in Serum Creatinine at Week 48 in the Blinded Phase
• Incidence of HIV-1 Infection Per 100 PY
• Percent Change From Baseline in Hip BMD at Week 96 in the Blinded Phase

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is an event rate, with person-time used as the exposure denominator. This differs from a binary outcome that counts how many participants experienced an event by a fixed time. A rate can incorporate unequal follow-up, provided that the definition of time at risk and event ascertainment are applied appropriately. Here, the registry describes the relevant event definition and the calculation of participant-years.

What does the rate ratio compare?

A rate ratio divides one group’s event rate by the other group’s rate. A ratio of 1 corresponds to equal rates; a ratio above or below 1 indicates the direction of the relative difference according to which group is in the numerator. Direction is essential when reading a ratio. The simple recalculation is explicitly oriented as TVD compared with DVY, whereas the registry’s reported rate ratio is 0.468 for the groups listed in the order Descovy and Truvada. The two estimates should not be read as if they necessarily used the same orientation or analysis method.

The recalculated comparison uses posted group-level rate summaries and is unadjusted. It gives a rate ratio of 2.138, a 95% confidence interval from 0.800 to 5.711, and an unadjusted p-value of 0.13. It is a straightforward comparison of the posted summaries, not a reconstruction of the sponsor’s full statistical analysis. Since the registry’s own analysis is also reported, the sponsor’s analysis takes precedence when describing the trial’s formal result.

What does a confidence interval convey?

A confidence interval represents uncertainty in an estimate under the statistical method used. A narrower interval indicates greater precision on the scale of that estimate; a wider interval indicates less precision. For a rate ratio, an interval that includes 1 is compatible with equal rates under the interval procedure. It is also compatible with values on either side of 1 when the interval extends across it. This interpretation is general and does not establish the probability that a particular value is true.

The group-level rate intervals and the comparative rate-ratio interval answer related but different questions. Each group’s interval describes uncertainty around that group’s rate. The rate-ratio interval describes uncertainty around the relative comparison. Separate group intervals should not be used as a substitute for an interval calculated directly for the comparison.

Why might the methods differ?

The registry’s reported analysis is labeled non-inferiority and reports a rate ratio of 0.468 with a 95% confidence interval from 0.191 to 1.149. The method field for that analysis is not reported in the registry record. The simple recalculation is unadjusted and derives from the posted summary statistics; it is not a substitute for the trial’s formal analysis. The registry record does not report the non-inferiority margin, the detailed model specification, covariate adjustment, or other analysis details needed to reproduce that formal result.

For count outcomes observed over person-time, a Poisson framework is one general approach to modeling event rates. The recalculated comparison is identified as using a Poisson rate-ratio approach. In general, Poisson methods relate event counts to exposure time, but their assumptions and any adjustments must be considered when evaluating a formal analysis. The registry record does not provide enough detail to establish the sponsor’s specific model or to assess all of its assumptions.

Why can over-dispersion matter?

As a general statistical issue, a basic Poisson model assumes that the variability in counts follows a particular relationship to the expected count. If observed variability is greater than that assumption allows, uncertainty can be understated unless the analysis accounts for over-dispersion or another appropriate structure. This is a general consideration for rate analyses, not a claim that over-dispersion occurred in this study. The registry record does not report an over-dispersion assessment or a model adjustment for it.

How should p-values be read?

The recalculated p-value is unadjusted. A p-value describes how incompatible the observed data are with a specified null model under the analysis assumptions; it is not the probability that the null hypothesis is true and does not measure clinical importance. The reported sponsor analysis has no p-value listed in the registry record. Its non-inferiority label cannot be fully evaluated without the margin and decision rule.

Several analysis details remain unreported in the registry record, including a full statistical-analysis plan, how missing primary endpoint data were handled, and whether interim analyses were conducted. The record also does not state the original design assumptions or sample-size justification. These absences limit reconstruction of the trial’s formal inferential procedures and should be kept distinct from the descriptive estimates that are posted.

11. Confidence Intervals and Precision

The primary group rates are reported with 95% confidence intervals: 0.16 HIV-1 infections per 100 PY, with an interval from 0.064 to 0.33, for Descovy (DVY); and 0.342 per 100 PY, with an interval from 0.191 to 0.564, for Truvada (TVD). These intervals describe uncertainty around the group-specific rates, not a direct interval for the difference or ratio between groups.

For the unadjusted comparison of TVD with DVY, the recalculated rate ratio is 2.138 and its 95% confidence interval ranges from 0.800 to 5.711. The interval includes 1, the value corresponding to equal rates, and spans a broad range of relative comparisons. That breadth indicates limited precision in the recalculated estimate. The unadjusted p-value is 0.13, which is consistent with the uncertainty conveyed by the interval; neither statistic establishes the probability that the groups have equal rates.

The registry’s own reported non-inferiority analysis gives a rate ratio of 0.468 and a 95% confidence interval from 0.191 to 1.149. That interval also includes 1. The sponsor’s estimate is the formal analysis to prioritize, but the registry record does not report its non-inferiority margin or p-value. Consequently, the interval can be described, while the non-inferiority decision rule cannot be independently reconstructed from the posted information.

Confidence intervals are not guarantees that the true value lies within a particular interval, nor do they describe the range of individual outcomes. Their precision depends on the data and methods used. Differences in orientation and analysis method matter when comparing the sponsor’s estimate with the unadjusted recalculation; apparent numerical contrast should not be treated as a contradiction without the underlying analysis details.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design justification. For the primary rate comparison, the figures are expressed as total numbers of events, rather than participants per arm. For the secondary continuous outcomes, the displayed figures are participants per arm. The unit differs because the primary endpoint is a time-at-risk event rate, while the secondary outcomes are continuous measurements.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row considers an effect equal to 100%, 75%, or 50% of the observed effect. The registry record does not report the original trial’s sample-size assumptions or justification, so these illustrations should not be read as the assumptions used to design this trial.

The 80% power column indicates the planning quantity needed for an analysis to have an 80% chance of detecting the stated effect under those assumptions, if that effect were present. The 90% power column uses the corresponding 90% target. For the primary endpoint, those quantities are total events; for continuous secondary endpoints, they are participants per arm. Power is conditional on the stated effect and assumptions, not a measure of the result’s importance.

Smaller effects require more information to detect, so the planning figures increase as the effect considered is reduced from the observed effect. These are planning illustrations, not observed power. They do not describe the power actually achieved in this trial, and the observed results cannot be used to establish that the study was adequately or inadequately designed.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 0.0016; treatment rate λ₁ = 0.0034 events per patient-year; follow-up T = 0.92 years.
2. n = (1.96 + 0.842)² × (1/0.0016 + 1/0.0034) / (0.92 × [ln(2.138)]²) = 13,564.9, rounded up to 13,565 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
lambda0 <- 0.0016                      # control rate, events per patient-year
lambda1 <- 0.00342                      # treatment rate
tt      <- 0.919892679187428                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^2), 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(2842086)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 13,565 (80% power), 18,160 (90% power)
 75% of observed effect: n per arm = 25,723 (80% power), 34,436 (90% power)
 50% of observed effect: n per arm = 62,250 (80% power), 83,335 (90% power)
Simulated power, Poisson counts, n = 13,565 per arm: 0.824
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.645

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The registry’s own reported analysis is labeled non-inferiority and gives a rate ratio of 0.468, with a 95% confidence interval from 0.191 to 1.149. The groups are listed as Descovy (DVY) and Truvada (TVD). The method and p-value are not reported in the registry record, and the non-inferiority margin is not reported there either.

The recalculated comparison uses the posted arm-level rates and is oriented as TVD compared with DVY. It is an unadjusted rate-ratio re-calculation, with an estimate of 2.138, a 95% confidence interval from 0.800 to 5.711, and an unadjusted p-value of 0.13. The different orientation and analysis approach mean that these figures should not be presented as though they were the sponsor’s formal estimate.

The sponsor’s own analysis takes precedence over the unadjusted re-calculation. Its non-inferiority label indicates the type of analysis reported, but the posted information is not enough to independently determine whether the pre-specified non-inferiority criterion was met. That assessment would require the margin and decision rule, which are not reported in the registry record. The fact that the discrepancy flag is false does not supply those missing details or make the two calculations interchangeable.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when statistical tests are conducted for multiple outcomes, time points, comparisons, or subgroups. As a general principle, the more tests considered, the greater the chance that at least one result will appear noteworthy by chance if no multiplicity strategy is applied. This does not mean that any particular secondary finding is false; it means that interpretation should account for the analysis family and any pre-specified control of error rates.

The registry lists 16 outcome measures, 14 analyses, and 15 posted secondary outcomes. These listings show that results extend beyond the primary endpoint, but they do not reveal the full testing hierarchy or whether adjustments were planned or applied. A multiplicity strategy is not reported in the registry record. The displayed unadjusted p-values for secondary recalculations should therefore not be read as if they necessarily account for all testing across the study.

Missing-data handling is also important. Participants may lack a measurement or discontinue before a scheduled assessment, and the analysis approach can affect estimates and uncertainty. The primary analysis population is defined, but the registry record does not report a detailed missing-data strategy for the primary endpoint or the secondary outcomes. The primary follow-up timeframe includes permanent discontinuation as part of the stated assessment rule, but that wording alone does not explain how participant-time or missing HIV assessments were handled in the analysis.

The record identifies a Full Analysis Set for the primary endpoint: randomized participants who received at least 1 dose, were not HIV positive on Day 1, and had at least 1 postbaseline HIV laboratory assessment. This definition is informative but does not establish the number excluded from the analysis or the reasons for any exclusions. Nor does it specify whether sensitivity analyses were conducted.

The registry record does not report a complete statistical-analysis plan, interim-analysis details, or the original sample-size justification. These limitations restrict assessment of pre-specification and robustness. They should be distinguished from the posted estimates themselves, which can be described, but do not resolve questions about unreported analytic decisions.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: appendicitis (0.4%), suicidal ideation (0.3%), atrial fibrillation (0.3%), cellulitis (0.3%), acute kidney injury (0.3%).

The registry lists serious adverse events for 202 of 2694 participants at risk in the Descovy group and 186 of 2693 at risk in the Truvada group. Deaths are listed as 3 in each group. Other adverse events are listed for 2258 of 2694 participants at risk in the Descovy group and 2229 of 2693 at risk in the Truvada group. These are posted counts and denominators; they should be read with the registry’s event definitions and collection procedures in mind.

The most frequent serious-event terms listed include appendicitis at 0.4%, suicidal ideation at 0.3%, atrial fibrillation at 0.3%, cellulitis at 0.3%, acute kidney injury at 0.3%, and hepatitis A at 0.2%. These terms are the listed events, not a complete account of every possible safety outcome. The registry record does not provide enough detail to infer causation, timing, severity beyond the serious-event classification, or how events were adjudicated.

Comparing adverse-event counts alone does not establish that one group is safer. Interpretation depends on definitions, exposure and follow-up, and the full safety analysis. The listed figures describe what the registry reports and should not be treated as medical advice.

17. What the Result Does, and Does Not, Mean

The primary outcome measures HIV-1 infection incidence per 100 person-years in the study’s defined analysis population and assessment period. The posted arm-level rates and their confidence intervals describe the observed infection-rate estimates. The unadjusted recalculation compares those rates, while the registry’s own analysis reports a non-inferiority rate ratio. These analyses have different orientations and should not be conflated.

The recalculated rate ratio’s confidence interval includes 1 and is broad. This means the unadjusted estimate is imprecise and does not rule out equal rates on the basis of that interval. The sponsor’s reported interval also includes 1, but a non-inferiority interpretation depends on the pre-specified margin and decision rule. Those details are not reported in the registry record, so the non-inferiority label alone does not establish that a criterion was met.

The results do not establish that either treatment works or does not work. They describe outcomes observed in this randomized study, as reported in the registry, and the degree of statistical precision conveyed by the stated intervals. They do not determine whether the observed differences are clinically important, and they do not address every outcome that may matter to participants or clinicians.

Nor do the posted results establish what would happen in populations outside the study’s stated group of men and transgender women who have sex with men and are at risk of HIV-1 infection. The registry’s Full Analysis Set definition and follow-up rules are part of the context for interpretation. Application beyond those criteria requires evidence not contained in the registry record.

The study is listed as terminated, but the reason is not reported in the registry record. Termination status does not, by itself, explain the results or imply a benefit, harm, or lack of effect. The secondary findings and safety listings offer additional context, but they do not replace the primary endpoint or resolve the unreported analysis details.

18. Why This Trial Matters Statistically

This study illustrates why event rates and person-time need to be interpreted together. The primary measure relates infections to time at risk, so it is not simply a comparison of the number of participants with an event. The registry’s infection definition and follow-up rules also show how endpoint construction affects what the rate represents.

It also illustrates the difference between a posted formal analysis and a simple re-calculation from group summaries. The registry reports a non-inferiority rate ratio, while the unadjusted re-calculation is oriented in the opposite group order and uses a direct comparison of the posted rates. Correct interpretation requires attention to the estimand, direction, method, and decision rule. Where the formal analysis details are absent, the re-calculation cannot fill those gaps.

Precision is another central statistical issue. The primary re-calculated interval spans a broad range and includes the value corresponding to equal rates. A point estimate on its own would conceal that uncertainty. Confidence intervals make the limits of the evidence more visible, while the absence of the sponsor’s non-inferiority margin limits what can be concluded from its reported estimate.

The study’s multiple secondary outcomes make multiplicity and analysis planning relevant. Secondary measures can broaden the picture, but their interpretation depends on pre-specification, missing-data handling, and any adjustment for multiple testing. Those methods are not reported in the registry record. The case therefore demonstrates why numerical results and the analysis plan are both needed for a complete statistical reading.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The registry record does not report the reason the study was terminated. It also does not provide the non-inferiority margin or the detailed decision rule for the sponsor’s analysis, limiting independent evaluation of the analysis labeled non-inferiority. The method field and p-value for that reported analysis are not listed.

The record does not report a complete statistical-analysis plan, including the detailed model specification for the sponsor’s primary analysis, missing-data procedures, multiplicity strategy, or interim-analysis plan. The full follow-up distribution is also not reported, so the posted timeframe rules cannot be used to infer the actual amount of follow-up contributed by each group.

The primary Full Analysis Set definition is reported, but the registry record does not give the number of participants excluded from that analysis or reasons for exclusion. The sample-size illustrations are based on observed effects and stated planning assumptions; they are not the original trial design justification. Original sample-size assumptions are not reported in the registry record.

The listed safety results provide event counts, denominators, deaths, and selected serious-event terms, but they do not by themselves establish causation or provide a complete comparative safety assessment. The registry record also describes open-label phases and an extension option, but does not establish participation or completion in those phases. These gaps limit interpretation of outcomes beyond the blinded primary assessment period.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate the Safety and Efficacy of Emtricitabine and Tenofovir Alafenamide (F/TAF) Fixed-Dose Combination Once Daily for Pre-Exposure Prophylaxis in Men and Transgender Women Who Have Sex With Men and Are At Risk of HIV-1 Infection — NCT02842086.
• Registry record last updated 2026-09-08; status last verified 2026-08.
• Results first posted 2020-03-17.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT02842086 is a randomized, double-blind, parallel-group Phase 3 study sponsored by Gilead Sciences. It compared daily F/TAF with daily F/TDF for HIV-1 pre-exposure prophylaxis in men and transgender women who have sex with men and are at risk of HIV-1 infection. The registry lists enrollment of 5399 and a terminated study status.

The primary endpoint was HIV-1 infection incidence per 100 person-years. The posted rates are 0.16 for Descovy (DVY) and 0.342 for Truvada (TVD), with 95% confidence intervals of 0.064 to 0.33 and 0.191 to 0.564, respectively. The registry’s reported non-inferiority analysis gives a rate ratio of 0.468, with a 95% confidence interval from 0.191 to 1.149. A separate unadjusted re-calculation is less precise and is not a substitute for the sponsor’s analysis.

Secondary outcomes and adverse-event listings add context, but interpretation is limited by unreported details, including the non-inferiority margin, full analysis plan, missing-data methods, and multiplicity strategy. The reason for termination is not reported in the registry record.