Comparative Trial Of Maraviroc Versus Emtricitabine/Tenofovir Both With Darunavir/Ritonavir In Antiretroviral-Naive Patients Infected With CCR5 Tropic HIV 1: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparative Trial Of Maraviroc Versus Emtricitabine/Tenofovir Both With Darunavir/Ritonavir In Antiretroviral-Naive Patients Infected With CCR5 Tropic HIV 1 (NCT01345630), a randomized phase 3 study. The primary outcome is Percentage of Participants With Plasma HIV-1 RNA <50 Copies/mL..

2. Clinical Question

The endpoint captures whether viral load was below the specified threshold at the assessment time, rather than the size of any change among participants who remained in follow-up. Under the stated FDA Missing, Switch, Discontinuation'=Failure Snapshot algorithm, participants with missing measurements, prohibited-regimen switches, study or drug discontinuation for any reason, or death were counted as failures. The primary result therefore reflects both observed viral-load status and the algorithm’s handling of these events.

The registry reports 77.3% for maraviroc plus darunavir/ritonavir and 86.8% for emtricitabine/tenofovir plus darunavir/ritonavir. The recalculated unadjusted risk difference, comparing the latter group with the former, is 0.095, with a confidence interval from 0.042 to 0.148. These figures describe the posted outcome; interpretation as a non-inferiority finding also depends on the sponsor’s analysis and a prespecified margin, which is not reported in the registry record.

3. Trial Design

This was a Phase 3, randomized, double-blind, parallel-group trial sponsored by ViiV Healthcare. It enrolled 813 participants and compared two once-daily regimens, each combining darunavir/ritonavir with a different accompanying antiretroviral regimen. The placebo components supported the double-blind comparison: each group received placebo corresponding to the other group’s study treatment.

The primary endpoint was assessed at Week 48. The registry describes the Full Analysis Set as all randomized participants who received at least one dose of study drug. The posted primary arm counts are 396 for maraviroc plus darunavir/ritonavir and 401 for emtricitabine/tenofovir plus darunavir/ritonavir. Missing primary outcome values were handled according to the FDA MSDF Snapshot algorithm, which treated missing measurements and specified treatment changes or discontinuations as failures.

The registry lists the study as terminated. The reason for termination, whether termination affected follow-up or endpoint collection, and the timing or circumstances of the decision are not reported in the registry record. The registry also does not report the trial’s original sample-size assumptions or a detailed statistical analysis plan. Those omissions matter when interpreting a study designed around non-inferiority: the intended margin and the formal analysis choices are needed to understand how the trial’s objective was evaluated.

Other posted outcomes cover adverse events, laboratory values, screening tropism tests, and peripheral fat distribution. The listed secondary outcomes extend to Week 96 for some safety assessments, while the viral-load and DEXA outcomes have Week 48 timeframes. The registry record lists 25 outcome measures and 14 analyses, but the existence of multiple outcomes does not by itself establish which were confirmatory or how multiplicity was handled.

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: Participants were randomized to undergo either genotype testing or enhanced Trofile assay (ESTA) in a 1:1 ratio. Among participants who were identified as being infected with R5 tropic HIV-1 by either testing methods, 813 were randomized in a 1:1 ratio to receive 96-week treatment either in the MVC+DRV/r arm or in the FTC/TDF+DRV/r arm.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) consisted of all randomized participants who received at least one dose of the study drug. The missing value was imputed per FDA's MSDF Snapshot algorithm as described under "Outcome Measure Description" above.

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.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Plasma HIV-1 RNA <50 Copies/mL., measured over Week 48.

The primary endpoint is the percentage of participants with plasma HIV-1 RNA <50 copies/mL at Week 48. It represents the proportion meeting a threshold for viral suppression at a specified visit window. A threshold-based endpoint is clinically and statistically interpretable as a responder proportion: each participant is classified according to whether the measured viral load meets the criterion.

The registry specifies the FDA Missing, Switch, Discontinuation'=Failure Snapshot algorithm. It uses the plasma HIV-1 RNA result in the Week 48 visit window, follows a virology-first principle, and counts missing measurements, switching to a prohibited antiretroviral regimen, discontinuation from the study or study drug for any reason, and death as failures. This approach avoids limiting the endpoint calculation to participants with an available Week 48 viral-load value, but it means the outcome reflects both virologic status and the specified handling of intercurrent events.

The posted percentages are 77.3% for maraviroc plus darunavir/ritonavir and 86.8% for emtricitabine/tenofovir plus darunavir/ritonavir. These are descriptive arm results under the stated algorithm. For the non-inferiority question, their interpretation depends on the treatment contrast, its uncertainty, the planned margin, and the sponsor’s formal analysis. The non-inferiority margin and full analysis method are not reported in the registry record.

7. Results Posted in the Registry

• FTC/TDF+DRV/r: 86.8% (348/401) versus 77.3% (306/396) on control; risk difference 9.5 percentage points (95% CI 4.2 to 14.8), risk ratio 1.12 (1.05–1.20); unadjusted two-proportion z-test p = <0.001.

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.

Number of Participants With Grade 3 or 4 AEs

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • FTC/TDF+DRV/r: 17.7% (71/401) versus 16.4% (65/396) on control; risk difference 1.3 percentage points (95% CI -3.9 to 6.5), risk ratio 1.08 (0.79–1.47); unadjusted two-proportion z-test p = 0.628.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FTC/TDF+DRV/r and the control. The interval gives the range of effects that remain compatible with the data.

The Relationship Between the Proportion of Participants With Plasma HIV-1 RNA <50 Copies/mL at the Week 48 and the Screening Tropism Test (Genotype Test or ESTA).

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • FTC/TDF+DRV/r: 1.0% (4/401) versus 0.8% (3/396) on control; risk difference 0.2 percentage points (95% CI -1.1 to 1.5), risk ratio 1.32 (0.30–5.85); unadjusted two-proportion z-test p = 0.717.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FTC/TDF+DRV/r and the control. The interval gives the range of effects that remain compatible with the data.

Changes in Peripheral Fat Distribution Using Dual Energy X-ray Absorptiometry [DEXA] Scan From Baseline and at Week 48.

• 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 errors.
• Result:
  • FTC/TDF+DRV/r: mean -257.50 versus -181.60 on control; difference -75.90 (95% CI -1,638 to 1,486), standardized effect d = -0.02; z-test p = 0.924.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FTC/TDF+DRV/r and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover a broad set of questions: adverse-event frequency and severity, laboratory abnormalities, screening tropism testing in relation to viral suppression, and peripheral fat distribution. Their timeframes and outcome types vary, so they do not form a single coherent replication of the Week 48 primary comparison. The overall pattern should be read as additional context, not as a direct substitute for the primary endpoint.

The posted secondary results do not all point to a single confirmatory conclusion. The safety outcomes describe event counts, while the tropism and DEXA outcomes involve different definitions and analysis methods. Some secondary comparisons have uncertainty spanning no difference, and the registry includes a small DEXA analysis subset. The record does not report a prespecified hierarchy linking these outcomes to the primary endpoint or a multiplicity adjustment.

Unadjusted secondary results carry less weight because repeated testing across many outcomes increases the possibility of chance findings. In addition, a secondary endpoint may be less precisely estimated, may involve a different analysis population, and may not have been powered for a reliable treatment comparison. The registry lists 24 posted secondary outcomes, but does not report which were designated confirmatory or how their tests were controlled.

Accordingly, secondary findings can help identify areas for further examination, but they should not be used selectively to declare that the primary result is supported or contradicted. Their interpretation depends on endpoint definitions, missing-data handling, analysis methods, and the broader testing plan, several of which are not reported in the registry record.

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

• Frequency of Adverse Events (AE).
• Number of Participants With Grade 3 or 4 AEs
• Number of Participants Who Discontinued Due to AEs
• Number of Treatment-related AEs
• Number of Participants With Treatment-emergent Serious Adverse Events
• Number of Participants With Abnormal Laboratory Values
• Severity of Abnormal Laboratory Values
• The Relationship Between the Proportion of Participants With Plasma HIV-1 RNA <50 Copies/mL at the Week 48 and the Screening Tropism Test (Genotype Test or ESTA).

9. Statistical Interpretation

10. Statistical Methods Explained

Comparing responder proportions. The primary outcome is binary at the participant level: each participant is counted as having met or not met the plasma HIV-1 RNA threshold at Week 48 under the Snapshot rule. The arm percentage is the proportion meeting that definition. A risk difference expresses the difference between two such proportions on an absolute scale. The recalculated contrast is reported for emtricitabine/tenofovir plus darunavir/ritonavir relative to maraviroc plus darunavir/ritonavir. Positive values therefore indicate a higher observed response proportion in the former group under that calculation’s stated direction.

A confidence interval describes a range of values compatible with the data under the interval method and its assumptions. Its width reflects precision: an interval spanning a broad range leaves more uncertainty about the size of the contrast. A p-value summarizes how incompatible the observed data are with a specified null hypothesis under a statistical model; it does not measure the probability that a treatment is effective, nor does it answer the non-inferiority question unless interpreted against the planned margin and analysis.

Non-inferiority objective. In general, a non-inferiority trial asks whether the experimental regimen is not worse than the comparator by more than a clinically selected margin. The margin defines the largest loss that would still be considered compatible with non-inferiority. The confidence interval and its orientation must be assessed relative to that margin, using the trial’s planned analysis population and method. The registry labels the reported primary analysis as non-inferiority or equivalence but does not report the margin or the statistical method. Without those details, the formal decision rule cannot be reconstructed from the registry record.

Missing-outcome handling. The primary endpoint uses the FDA MSDF Snapshot algorithm. As described in the registry, participants with missing Week 48 viral-load results, switches to prohibited antiretroviral regimens, discontinuation from the study or study drug for any reason, or death were classified as failures. This is a composite operational rule for deriving the responder status. It can produce a different result from an analysis restricted to participants with observed viral-load measurements, because treatment changes and missingness affect the endpoint classification. The record does not report additional sensitivity analyses for missing data.

Analysis populations. The Full Analysis Set consists of randomized participants who received at least one dose of study drug. This population is defined in the registry for the primary endpoint. The record does not give further detail about other populations used for the sponsor’s non-inferiority analysis, such as whether a per-protocol analysis was also conducted. That distinction can matter in non-inferiority settings, where departures from assigned treatment and analysis-population choices may affect the estimated contrast.

Unadjusted recalculations. The recalculated estimates are simple, unadjusted comparisons derived from posted summary statistics. They do not account for covariates, stratification factors, site, or any other design features unless those are already reflected in the posted summaries; the registry record does not give such details for the primary recalculation. The recalculated p-value should therefore be read as a descriptive analysis using the available arm counts, not as the trial’s complete prespecified inferential analysis. The sponsor’s own reported analysis is a separate result and should be interpreted according to its stated parameter and any available method information.

Secondary outcomes and multiple testing. When a study assesses multiple outcomes, testing each at a conventional significance threshold can increase the chance of at least one apparently notable result by chance. General approaches include prespecifying a testing hierarchy, adjusting significance thresholds, or treating secondary findings as exploratory. The registry record does not report how multiplicity was addressed or which outcomes, if any, were controlled as a confirmatory family. For that reason, secondary p-values and estimates should not be read as if each independently established a definitive finding.

Several secondary endpoints are binary, including Grade 3 or 4 adverse events, while the DEXA outcome is reported as a least-squares mean with a standard error. These parameters answer different questions and require different interpretations. An arm proportion describes how many participants met a binary definition; a mean difference describes a contrast in a continuous measurement. The reported DEXA sponsor analysis uses ANCOVA, whereas the posted recalculation is an unadjusted comparison. Those methods need not yield identical estimates because adjustment and model specification can change the target estimate and its uncertainty.

Over-dispersion is relevant in general when observed variability in count data exceeds what a simple model assumes; an appropriate model may then need to allow extra variability. The primary endpoint is a binary participant outcome, not a count rate with a dispersion parameter, and no over-dispersion parameter is reported. No specific dispersion adjustment or other model feature should be inferred from the registry information.

11. Confidence Intervals and Precision

The primary unadjusted risk difference is 0.095, with a 95% confidence interval from 0.042 to 0.148. The interval gives a range of plausible values for the population contrast under the calculation’s assumptions. It excludes zero, consistent with the reported unadjusted p-value of p <0.001. This does not establish non-inferiority, because non-inferiority requires comparison with the prespecified margin, which is not reported in the registry record.

The sponsor-reported primary analysis gives a mean difference (final values) of -9.54, with a 95% confidence interval from -14.83 to -4.24. The registry record does not describe the method, scale interpretation, or non-inferiority margin for this analysis. It should therefore be kept distinct from the recalculated risk difference rather than treated as the same estimate expressed in another format.

Confidence intervals express uncertainty in an estimate, not the range of individual participant outcomes. A narrower interval indicates greater statistical precision for the contrast, while a wider interval indicates less precision. Precision depends on factors such as the number of observations, outcome variability, and the statistical method. The primary arm counts are 396 and 401, but the interval also depends on the endpoint definition and calculation method.

Secondary estimates have their own uncertainty and, in some cases, smaller analysis subsets or sparse events. Those limits affect how strongly secondary patterns can be interpreted. The DEXA estimate, for example, comes from analysis groups of 52 and 56 participants and has a broad reported interval; the registry’s sponsor analysis and unadjusted recalculation also use different methods. Intervals across different outcomes should not be compared as if they answered the same question.

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 calculation. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The figures for these non-time-to-event outcomes are participants per arm; time-to-event planning figures, if present, would instead be total event counts. These figures are not observed power.

The 80% power column gives the illustrated number of participants per arm for a design that would have an 80% chance of detecting the specified effect under the listed assumptions, if the assumptions and effect were correct. The 90% column gives the corresponding planning number for a higher chance of detection. Power is a design property calculated before observing trial results under assumed conditions, not a measure of how persuasive the completed trial’s result is.

Rows for 100%, 75%, and 50% of the observed effect illustrate how the planning requirement changes when the target effect is smaller. A smaller effect is harder to distinguish from random variation, so more participants are required under otherwise unchanged assumptions. The observed effect may not be a reliable estimate of the effect expected in a future study, particularly when it is imprecise, so these values are scenarios rather than recommendations.

The registry record does not report the original sample-size justification or the assumptions used when the trial was designed. The posted illustrations should not be used to infer that the trial was adequately or inadequately powered for its intended non-inferiority objective. Such an assessment requires the original margin, assumptions, and planned analysis.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.773; treatment proportion p₁ = 0.868; average p̄ = 0.820.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5430 = 1.0642.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5388 = 0.4535.
4. n = (1.0642 + 0.4535)² / (0.0951)² = 254.7, rounded up to 255 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
p0 <- 0.772727272727273                          # control proportion
p1 <- 0.86783042394015                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1345630)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 255 (80% power), 341 (90% power)
 75% of observed effect: n per arm = 477 (80% power), 638 (90% power)
 50% of observed effect: n per arm = 1,125 (80% power), 1,505 (90% power)
power.prop.test: 254.7 
Simulated power at n = 255 per arm: 0.807 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports a sponsor analysis for the primary outcome labeled “Mean Difference (Final Values),” with an estimate of -9.54 and a 95% confidence interval from -14.83 to -4.24. It is classified as a non-inferiority or equivalence analysis, but the method, scale details, and non-inferiority margin are not reported in the registry record.

The recalculated primary comparison is an unadjusted risk difference based on the posted arm-level response counts and denominators. Its estimate is 0.095, with a 95% confidence interval from 0.042 to 0.148. Because the displayed parameters differ, the two results should not be treated as interchangeable or compared as though they were the same model estimate. The record does not explain how the sponsor’s reported contrast relates to the unadjusted risk difference.

The sponsor analysis is the trial’s own reported inferential result; the recalculation is a separate, transparent comparison of the posted summaries. Neither can be fully interpreted for non-inferiority without the margin and the analysis details. The registry’s discrepancy indicator is false, but the distinct parameter labels and missing method description remain important context for reading the results.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint uses an explicit missing-data and treatment-change rule: the FDA MSDF Snapshot algorithm counts a missing Week 48 viral-load result, a switch to a prohibited antiretroviral regimen, discontinuation from the study or study drug for any reason, or death as failure. This makes the endpoint definition clear about how those events affect responder status. It does not reveal how many participants were classified as failures for each reason, or whether additional sensitivity analyses were conducted; those details are not reported in the registry record.

The Full Analysis Set includes randomized participants who received at least one dose of study drug. This is the population specified for the primary outcome. The registry does not describe whether the formal non-inferiority analysis also used another population, such as a per-protocol set, or how departures from assigned treatment were handled in that analysis. Those details are particularly relevant when evaluating a non-inferiority claim.

The record lists numerous secondary outcomes and analyses, but does not report a multiplicity plan, a testing hierarchy, or whether any secondary outcomes were designated confirmatory. Without such information, nominal secondary p-values should be interpreted cautiously because the chance of a false-positive result can increase when many hypotheses are examined. The registry also does not report interim analyses, stopping rules, or whether any adjustment was made for repeated looks at the data.

These omissions do not change the posted endpoint values, but they limit reconstruction of the trial’s full inferential framework. In particular, the registry does not provide the non-inferiority margin, detailed analysis populations, or the original statistical plan. The available record supports a description of the posted results and their uncertainty, but not a complete audit of the prespecified testing procedure.

16. Safety Results

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

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: colitis (0.5%), chest pain (0.5%), hodgkin's disease (0.5%), depression (0.5%), acute hepatitis c (0.5%).

The registry reports serious adverse events in 41 of 396 participants in the maraviroc plus darunavir/ritonavir group and 40 of 401 participants in the emtricitabine/tenofovir plus darunavir/ritonavir group. The groups at risk are the respective posted arm counts. These are descriptive counts; they do not alone establish whether the regimens differ in safety, and no comparative serious-adverse-event analysis is reported in the safety summary.

The listed serious event terms include colitis, chest pain, Hodgkin's disease, depression, acute hepatitis C, and toxicity to various agents, each reported as 0.5%. The registry also gives other adverse-event counts, but those are distinct from serious adverse events and should not be combined with them. Death counts are not reported in the safety summary.

Safety counts depend on the registry’s event definitions, observation period, and collection methods. The available record does not provide enough detail to assess event timing, exposure-adjusted rates, or causal attribution for these serious events. The figures are best read as the posted numbers of affected participants in each arm, not as proof of a treatment-related difference.

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

The posted primary results show that 77.3% of participants assigned to maraviroc plus darunavir/ritonavir and 86.8% assigned to emtricitabine/tenofovir plus darunavir/ritonavir met the Week 48 viral-load criterion under the stated Snapshot algorithm. The unadjusted risk-difference estimate and confidence interval quantify the observed contrast and its statistical uncertainty. The comparison is descriptive and does not, by itself, establish the trial’s stated non-inferiority conclusion.

A non-inferiority interpretation requires a prespecified margin and a formal analysis whose estimate and uncertainty are evaluated against that margin. The margin and sufficient methodological detail are not reported in the registry record. The sponsor’s posted analysis is labeled non-inferiority or equivalence, but the registry does not state the decision rule or explain the displayed estimate’s scale. A reader therefore cannot determine from this record alone whether the planned non-inferiority criterion was met.

The results also do not establish that either regimen is appropriate for an individual. They describe trial outcomes in the enrolled population and under the registry’s endpoint definition. The trial was terminated, but the reason and implications are not reported in the registry record. The registry information does not allow conclusions about the cause of termination or whether it changed the planned analyses.

Secondary and safety findings add context but are not a substitute for the primary analysis. Differences in endpoint definitions, follow-up times, analysis subsets, and the unreported multiplicity plan limit how much can be inferred by comparing them with one another. The statistical record supports a careful account of the observed proportions and uncertainty, while leaving key elements of the formal non-inferiority assessment unresolved.

18. Why This Trial Matters Statistically

This trial illustrates why a non-inferiority objective cannot be judged from arm percentages alone. The primary outcome is straightforward to describe as a responder proportion, and the unadjusted risk difference provides an interpretable absolute contrast. But a non-inferiority claim depends on the margin and the analysis procedure, not simply on whether an estimate appears close to zero or whether a conventional superiority test is statistically significant.

It also highlights how endpoint rules shape a result. The Snapshot algorithm classifies missing measurements, treatment switches, discontinuations, and deaths as failures. That definition makes the primary endpoint a measure of response under a specified treatment-policy and follow-up framework, rather than a simple summary of available viral-load measurements. Understanding the rule is essential when reading the reported proportions.

The comparison between the sponsor’s reported analysis and the unadjusted recalculation demonstrates that different statistical summaries may target different parameters or apply different models. Clear reporting of the estimand, analysis method, population, margin, and confidence interval is needed to connect an observed contrast to the trial’s intended conclusion.

Finally, the registry includes a wide range of secondary outcomes, while the multiplicity approach is not reported. This is a common interpretive challenge: an extensive outcome list can offer useful descriptive context, but without a testing plan it cannot be treated as a collection of independent confirmatory findings. The record therefore makes the distinction between descriptive evidence and a fully documented confirmatory analysis especially important.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The principal limitation for interpreting the stated non-inferiority objective is that the non-inferiority margin is not reported in the registry record. The sponsor’s primary analysis is labeled non-inferiority or equivalence, but its method and scale details are also absent. This prevents evaluation of the formal decision rule against the reported interval.

The registry marks the study as terminated but does not report the reason, timing, or effect on follow-up and analysis. It also does not report the original sample-size justification, interim analyses, stopping rules, or a detailed statistical analysis plan. The posted planning illustrations use the observed effect and should not be mistaken for the original design basis.

The primary endpoint’s Snapshot rule is described, but the registry does not provide a breakdown of failures by missingness, treatment switch, discontinuation, or death, nor does it report additional missing-data sensitivity analyses. The Full Analysis Set is defined, but the population used for the sponsor’s formal non-inferiority result is not described.

Secondary findings are difficult to interpret as a group because the registry does not report a multiplicity strategy or identify confirmatory secondary outcomes. Some outcomes use different timeframes, methods, and analysis subsets. The DEXA comparison, for instance, involves a subset of participants and has a sponsor-reported ANCOVA analysis alongside an unadjusted recalculation. These limits make broad cross-outcome conclusions inappropriate from the registry record alone.

The safety summary reports participant counts but does not provide exposure-adjusted rates or enough event-level detail to assess timing and attribution. These are limitations of the available registry reporting, not evidence that a particular analysis or event pattern was absent.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Comparative Trial Of Maraviroc Versus Emtricitabine/Tenofovir Both With Darunavir/Ritonavir In Antiretroviral-Naive Patients Infected With CCR5 Tropic HIV 1 — NCT01345630.
• Registry record last updated 2016-01-14; status last verified 2015-12.
• Results first posted 2016-01-14.
• 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

NCT01345630 is a randomized, double-blind, Phase 3 parallel-group trial comparing maraviroc plus darunavir/ritonavir with emtricitabine/tenofovir plus darunavir/ritonavir in antiretroviral-naive patients with CCR5-tropic HIV-1. The registry reports enrollment of 813 and a terminated study status.

The primary endpoint was plasma HIV-1 RNA <50 copies/mL at Week 48, assessed under the FDA MSDF Snapshot algorithm. The posted proportions were 77.3% and 86.8%, respectively. An unadjusted risk-difference recalculation is 0.095, with a 95% confidence interval from 0.042 to 0.148. The registry also reports a sponsor analysis labeled non-inferiority or equivalence, but the margin and method needed to assess that conclusion are not reported in the registry record.

Secondary outcomes cover safety, tropism testing, and peripheral fat distribution. Their interpretation is limited by differing endpoints and methods and the absence of a reported multiplicity plan. The registry does not explain the study termination or provide the full original design and analysis assumptions.