Study to Evaluate Switching From Regimens Consisting of a Ritonavir-boosted Protease Inhibitor (PI) and Two Nucleoside Reverse Transcriptase Inhibitors (NRTIs) to a Fixed-dose Tablet Containing Emtricitabine/Rilpivirine/Tenofovir DF: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate Switching From Regimens Consisting of a Ritonavir-boosted Protease Inhibitor (PI) and Two Nucleoside Reverse Transcriptase Inhibitors (NRTIs) to a Fixed-dose Tablet Containing Emtricitabine/Rilpivirine/Tenofovir DF (NCT01252940), a randomized phase 3 study. The primary outcome is Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 24 (FDA Snapshot Analysis).

2. Clinical Question

3. Trial Design

The registry describes a randomized, open-label, parallel-group Phase 3 study; the brief summary calls it Phase 3b. It was an active-controlled study sponsored by Gilead Sciences and enrolled 482 participants. The condition listed was HIV-1 infection. The study started in 2010-11, reached primary completion in 2012-01, and is recorded as completed.

Participants assigned to FTC/RPV/TDF switched from their existing regimen at the beginning of the study. Those assigned to Stay on Baseline Regimen (SBR)/Delayed Switch continued their existing PI+RTV and two-NRTI regimen through Week 24 and could switch to FTC/RPV/TDF at that visit. The planned comparison therefore concerns the initial period in which one group had switched and the other remained on baseline treatment. After the 48-week study analysis period, participants could continue FTC/RPV/TDF per protocol before switching to a commercially available source.

Open-label means treatment assignment was not masked. The record does not report a masking procedure. The randomized allocation supports a between-group comparison, while the open-label design means participants and study staff knew the assigned treatment. The available record does not report the randomization procedure, allocation ratio, or further operational details of the trial design.

The primary analysis population is described as the Full Analysis Set: randomized participants who received at least one dose of study drug. The Week 24 primary endpoint used the FDA snapshot analysis. Other posted outcomes include a Week 48 viral-load endpoint and CD4-count changes through Week 24 and Week 48. The registry lists 12 outcome measures and one posted analysis; details of the complete statistical analysis plan are not reported in the registry record.

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: 617 participants were screened.

Main Study Phase

Reasons for not completing this period:

Extension Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set: participants who were randomized into the study and received at least one dose of study drug.

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: Safety Analysis Set: participants who were randomized and received at least one dose of study drug

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 24 (FDA Snapshot Analysis), measured over Week 24.

The primary endpoint is the percentage of participants with HIV-1 RNA < 50 copies/mL at Week 24, analyzed using the FDA snapshot analysis. It is a binary outcome: each participant is classified according to whether the viral-load threshold is met for the analysis. The reported group percentages summarize the frequency of that outcome in each group, rather than the amount of change in viral load.

A threshold-based viral-load endpoint is used to describe virologic status at a prespecified follow-up time. The Week 24 assessment also aligns with the treatment contrast built into the design: the FTC/RPV/TDF group had switched at study start, while the SBR/Delayed Switch group remained on baseline treatment through that visit. After Week 24, the comparator group could switch, so a later comparison no longer represents the same initial treatment contrast.

The FDA snapshot approach is the named analysis method in the registry record. Its detailed rules for classifying missing or unavailable Week 24 results are not reported in the registry record. The primary endpoint therefore has a clear clinical measurement and assessment time, but the posted record does not provide all operational detail needed to reproduce the snapshot classification.

7. Results Posted in the Registry

• SBR/Delayed Switch: 89.9% (143/159) versus 93.7% (297/317) on control; risk difference -3.8 percentage points (95% CI -9.1 to 1.6), risk ratio 0.96 (0.90–1.02); unadjusted two-proportion z-test p = 0.144.

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.

Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 48 (FDA Snapshot Analysis)

• 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:
  • SBR/Delayed Switch: 92.1% (140/152) versus 89.3% (283/317) on control; risk difference 2.8 percentage points (95% CI -2.6 to 8.3), risk ratio 1.03 (0.97–1.10); unadjusted two-proportion z-test p = 0.335.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SBR/Delayed Switch and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Cluster of Differentiation 4 (CD4) Count Through Week 24

• 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:
  • SBR/Delayed Switch: mean 32.00 versus 20.00 on control; difference 12.00 (95% CI -18.60 to 42.60), standardized effect d = 0.08; z-test p = 0.442.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SBR/Delayed Switch and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in CD4 Count Through 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 deviations.
• Result:
  • SBR/Delayed Switch: mean -7.00 versus 10.00 on control; difference -17.00 (95% CI -47.26 to 13.26), standardized effect d = -0.12; z-test p = 0.271.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SBR/Delayed Switch and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results cover virologic status at Week 48 and changes in CD4 count through Week 24 and Week 48. The registry also lists outcomes involving fasting cholesterol measures, alongside other secondary measures. The secondary results span different endpoint types and follow-up times, so they do not all represent the same treatment contrast or answer the same question.

At a broad level, the Week 48 virologic outcome and CD4 changes provide context beyond the primary Week 24 snapshot. They should be viewed alongside, rather than as replacements for, the primary result. The delayed-switch group could change treatment at Week 24, so later outcomes reflect a different treatment history than the initial randomized comparison. Secondary findings can inform the overall description of the study, but they do not by themselves resolve the primary noninferiority question.

Unadjusted secondary comparisons carry less inferential weight when many outcomes are examined. In general, making multiple statistical comparisons increases the chance that some results appear notable by chance alone. The registry record does not report a multiplicity adjustment or a hierarchy controlling interpretation across secondary outcomes. Therefore, any unadjusted secondary p-values or intervals should be treated as exploratory unless a prespecified analysis plan states otherwise.

The registry lists 12 outcome measures and reports one analysis. A full account of all secondary analysis methods and results is not available in the registry record. The breadth of listed outcomes is useful for understanding what was assessed, but it does not establish that every outcome was tested in a way that supports confirmatory conclusions.

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

• Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 48 (FDA Snapshot Analysis)
• Change From Baseline in Cluster of Differentiation 4 (CD4) Count Through Week 24
• Change From Baseline in CD4 Count Through Week 48
• Change From Baseline in Fasting Total Cholesterol Through Week 24
• Change From Baseline in Fasting Total Cholesterol Through Week 48
• Change From Baseline in Fasting High-density Lipoprotein (HDL) Cholesterol Through Week 24
• Change From Baseline in Fasting HDL Cholesterol Through Week 48
• Change From Baseline in Fasting Direct Low-density Lipoprotein (LDL) Cholesterol Through Week 24

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary percentage represent?

The endpoint records whether each participant had HIV-1 RNA < 50 copies/mL at Week 24 under the FDA snapshot analysis. The group percentages are the proportions classified as meeting that endpoint. The comparison is binary, rather than a comparison of average viral-load values. The registry identifies the Full Analysis Set as randomized participants who received at least one dose of study drug.

What is a risk difference?

The recalculated risk difference subtracts the percentage in the FTC/RPV/TDF group from the percentage in the SBR/Delayed Switch group, using the comparison ordering stated in the analysis. It is expressed as a difference in proportions, not as a ratio. A value of zero represents no difference on this scale. The estimate of -0.037 is accompanied by a 95% confidence interval from -0.091 to 0.016. Because the interval spans zero, the posted unadjusted calculation does not distinguish a difference from no difference at the conventional two-sided 0.05 significance level; its p-value is 0.144.

This is a recalculation from posted summary statistics, not a substitute for the sponsor's analysis. It is unadjusted and does not reproduce any analysis procedures that are not documented in the registry record. The registry's sponsor result is labelled as a noninferiority or equivalence analysis and is reported on a Mean Difference (Net) scale. The two estimates should not be read as interchangeable.

How should a confidence interval be understood?

In general, a confidence interval describes the uncertainty of an estimate under the assumptions of the statistical method. It indicates which values are reasonably compatible with the data and method; it is not a guarantee that the true value lies within the particular interval. For the recalculated Week 24 difference, the interval includes zero and extends in both directions. That breadth means the estimate does not locate the group contrast precisely enough to rule out no difference or contrasts in either direction on this scale.

What does the p-value address?

In general, a p-value measures how unusual data at least as extreme as those observed would be under a specified null model. The unadjusted p-value of 0.144 is not a measure of clinical importance, and it is not the probability that the null hypothesis is true. Nor does a nonsignificant test establish equivalence or noninferiority. Those conclusions require a prespecified margin and the corresponding inferential procedure. The registry record does not report the sponsor's margin or full decision rule.

Why does timing matter?

The primary outcome is assessed at Week 24, when the randomized groups still represent immediate switch versus staying on baseline treatment. Participants in the delayed-switch group could change to FTC/RPV/TDF at the Week 24 visit. Thus, the Week 48 comparison follows a period in which the treatment contrast has changed. The Week 48 result is a separate endpoint and should not be interpreted as a continuation of an unchanged randomized comparison.

What assumptions are not visible in the recalculation?

The registry record names the endpoint method and analysis population, but it does not report all details needed to reconstruct the sponsor's statistical procedure. For example, the noninferiority margin, handling rules beyond the stated snapshot method, and complete model specification are not reported in the registry record. The recalculation uses posted summary results and should be understood as a simple unadjusted comparison, not as a reconstruction of the full trial analysis.

11. Confidence Intervals and Precision

The Week 24 recalculated risk difference is -0.037, with a 95% confidence interval from -0.091 to 0.016. The interval includes zero and allows values on either side of no difference. In practical statistical terms, the point estimate alone gives an incomplete account: the interval shows that the estimate remains uncertain and does not rule out a range of group contrasts.

Confidence intervals are useful because they combine the direction and size of an estimate with its sampling uncertainty. In general, a narrower interval indicates greater precision, while a wider interval indicates less precision. Precision is not the same as clinical importance, and an interval that includes zero does not prove that the groups are equivalent. The interval must be interpreted in relation to the study question and any prespecified decision margin.

The sponsor's posted noninferiority or equivalence result is 3.8, with a 95% confidence interval from -1.6 to 9.1. It is reported as Mean Difference (Net), not as the recalculated risk difference. The registry record does not give the margin or explain the direction convention sufficiently to assess the sponsor's noninferiority decision from the interval alone. The two intervals refer to different reported analyses and should not be compared as if they were estimates on one common scale.

The Week 24 primary result applies to the stated snapshot endpoint and Full Analysis Set. It does not quantify uncertainty for all secondary outcomes or for later follow-up. The posted results do not give confidence intervals for the individual group percentages. The risk-difference interval is therefore the principal precision summary for the unadjusted primary comparison.

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 planning illustrations translate an observed effect into hypothetical future study sizes. For the primary binary outcome, figures are participants per arm, not total participants or events. The illustrations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They consider detecting 100%, 75%, or 50% of the observed effect. The trial's original design assumptions, including its own sample-size justification, are not reported in the registry record.

The 80% power column describes a planning scenario in which a study designed to detect the stated effect would have an 80% chance of rejecting the null hypothesis under the specified assumptions, if that effect were the true effect. The 90% power column uses a higher chance of detecting the same stated effect and therefore generally requires more participants per arm. These are design probabilities under assumptions, not guarantees about a future result.

For the primary endpoint, planning for 100% of the observed effect gives 837 participants per arm for 80% power and 1,119 participants per arm for 90% power. Planning for 75% of the observed effect gives 1,410 participants per arm for 80% power and 1,887 participants per arm for 90% power. Planning for 50% of the observed effect gives 2,995 participants per arm for 80% power and 4,009 participants per arm for 90% power. The pattern illustrates that smaller effects require more participants to detect under the same planning assumptions.

These figures are planning illustrations based on the observed effect, not observed power. They are sensitive to the assumptions and to the observed effect used as their starting point. They do not establish that the completed trial was adequately or inadequately designed, because the original design rationale is not reported in the registry record.

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 = 0.937; treatment proportion p₁ = 0.899; average p̄ = 0.918.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3877 = 0.7599.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3868 = 0.3255.
4. n = (0.7599 + 0.3255)² / (-0.0375)² = 836.1, rounded up to 837 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 <- 0.936908517350158                          # control proportion
p1 <- 0.89937106918239                          # 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(1252940)
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 = 837 (80% power), 1,119 (90% power)
 75% of observed effect: n per arm = 1,410 (80% power), 1,887 (90% power)
 50% of observed effect: n per arm = 2,995 (80% power), 4,009 (90% power)
power.prop.test: 836.1 
Simulated power at n = 837 per arm: 0.812 (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 labelled noninferiority or equivalence: Mean Difference (Net) 3.8, with a 95% confidence interval from -1.6 to 9.1. It does not post a p-value for this analysis. The registry record does not report the noninferiority margin, the full analysis method, or sufficient detail about the estimate's direction convention to reconstruct the decision rule.

The recalculated primary comparison is a simple unadjusted risk difference from the posted group percentages and summary counts. It is -0.037, with a 95% confidence interval from -0.091 to 0.016 and p = 0.144. This is a different estimand and analysis from the sponsor's reported Mean Difference (Net). The recalculation is useful as a transparent description of the posted proportions, but it does not replace or reproduce the sponsor's noninferiority analysis.

The record does not flag a discrepancy between the posted and recalculated results. Even so, the results answer questions in different statistical frameworks. The sponsor's result should be interpreted using its stated noninferiority or equivalence framework, while the recalculated result describes an unadjusted between-group contrast and its interval. Without the margin and analysis details, a firm noninferiority decision cannot be independently assessed from the posted sponsor summary alone.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several endpoints, time points, or comparisons. In general, the more statistical tests conducted, the greater the chance that at least one result may appear unusual even when there is no underlying effect. Researchers can address this through prespecified outcome hierarchies or statistical adjustments, but those methods and their interpretation need to be reported.

The registry lists 12 outcome measures, including the Week 24 primary virologic endpoint, a Week 48 virologic endpoint, CD4-count changes, and lipid measures. It reports one analysis. The registry record does not report a multiplicity adjustment, a testing hierarchy for secondary outcomes, or enough of the statistical plan to determine how multiple comparisons were handled. Secondary results therefore warrant more caution than a single prespecified primary analysis, particularly if they are interpreted as confirmatory.

The primary analysis population is described as randomized participants who received at least one dose of study drug. The primary endpoint used the FDA snapshot analysis, but the detailed snapshot rules for participants with missing or unavailable Week 24 measurements are not reported in the registry record. The record does not give a full accounting of missing primary-outcome data or describe sensitivity analyses for missingness.

These omissions matter because missing outcomes can affect both the group percentages and the uncertainty around their comparison. In general, conclusions may depend on how unavailable results are classified and on whether missingness is related to outcome or treatment. No assumptions about those mechanisms can be made from the registry record. The available summary supports interpretation of the posted analysis, but not a complete independent audit of missing-data handling.

The stated Full Analysis Set is not the same as a statement that every randomized participant contributed an observed Week 24 outcome. The record describes inclusion in the analysis population by randomization and receipt of at least one dose, but does not provide the detailed participant flow or endpoint-specific missingness needed to assess all exclusions and classifications.

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: pneumonia (0.9%), angina unstable (0.7%), palpitations (0.7%), gastrointestinal haemorrhage (0.7%), chest pain (0.7%).

The registry reports serious adverse events for FTC/RPV/TDF in 21 participants among 317 at risk. For SBR/Delayed Switch through Week 24, it reports 8 participants among 159 at risk. After Week 24, the delayed-switch group is reported separately: 9 participants among 152 at risk. These are counts for the stated groups and exposure periods; the two delayed-switch periods should not be combined because the record presents them as distinct windows.

Other adverse events are reported for 150 participants among 317 at risk in the FTC/RPV/TDF group, 38 among 159 in the SBR/Delayed Switch group through Week 24, and 59 among 152 after Week 24. The registry lists pneumonia at 0.9%, with angina unstable, palpitations, gastrointestinal haemorrhage, chest pain, and subcutaneous abscess each at 0.7% among the serious-event terms reported.

These figures describe recorded events, not proof that a study drug caused them. The registry record does not report death counts. The record also does not provide enough detail in these summaries to assess event duration, severity beyond the serious-event classification, or adjusted comparisons between groups. Safety counts should be interpreted in light of the different exposure windows, especially after the delayed-switch group became eligible to change treatment.

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

The Week 24 results describe the percentage of participants classified as having HIV-1 RNA < 50 copies/mL under the FDA snapshot analysis. The posted percentages are high in both groups, and the unadjusted comparison has a confidence interval that includes no difference. This is evidence about the measured endpoint in this trial population at that time point; it is not a universal statement about all patients, treatment settings, or outcomes.

The study was designed to evaluate noninferiority, but a nonsignificant difference test is not enough to establish noninferiority. That conclusion depends on a prespecified margin and an analysis designed for that purpose. Although the registry reports a sponsor analysis labelled noninferiority or equivalence, it does not provide the margin or full decision details. The unadjusted recalculation should not be used as a substitute for those missing elements.

The Week 48 outcome has a different interpretation because participants in the SBR/Delayed Switch group could switch to FTC/RPV/TDF at Week 24. It therefore does not maintain the same contrast as the primary Week 24 comparison. CD4 and other secondary measures address additional aspects of outcome, but the registry record does not report multiplicity procedures, and secondary findings should not be treated as conclusive merely because they are posted.

Safety counts are descriptive and do not establish causation. They also cover different treatment periods in the delayed-switch group. Taken together, the posted data characterize the primary endpoint, selected secondary outcomes, and recorded adverse events. They do not provide a complete account of the statistical plan, missing-data assumptions, or all analysis details needed to independently reproduce the sponsor's conclusions.

No treatment recommendation follows from these statistics. Their interpretation is limited to the randomized, open-label study and the populations, endpoint definitions, and follow-up periods recorded in the registry.

18. Why This Trial Matters Statistically

This trial presents a useful statistical contrast between an immediate treatment switch and a delayed-switch strategy. The Week 24 assessment occurs while the comparator group is still on its baseline regimen, making that time point central to the initial randomized comparison. The possibility of switching after Week 24 also illustrates why follow-up timing matters: later results do not necessarily preserve the original treatment contrast.

The endpoint is a binary threshold measure, and the registry permits an unadjusted recalculation of the group difference from posted summaries. That makes the distinction between an observed percentage, a risk difference, and a noninferiority analysis especially important. The recalculated interval includes zero, while the sponsor's reported analysis is on a different stated scale and lacks the margin and full decision rule in the registry record. This is a practical example of why statistical summaries cannot be interpreted without knowing the estimand and design objective.

The record also illustrates the separate roles of primary and secondary outcomes. A prespecified primary endpoint is the main focus for the stated objective, whereas multiple secondary outcomes can broaden the description but introduce multiplicity concerns. Because the statistical plan and multiplicity handling are not reported, the strength of secondary evidence cannot be judged from the registry summary alone.

Finally, the available data distinguish descriptive safety counts from causal conclusions and show why exposure periods need to be read separately when treatment changes occur. Clear reporting of analysis populations, missingness, decision margins, and multiplicity would make the statistical conclusions easier to independently evaluate.

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 registry record does not report the sponsor's noninferiority margin or enough detail about the Mean Difference (Net) scale and decision rule to independently assess the sponsor's noninferiority conclusion. The unadjusted recalculation is not a replacement for that analysis, and the absence of a flagged discrepancy does not make the methods interchangeable.

Detailed rules for the FDA snapshot classification and a complete account of missing primary-outcome data are not reported in the registry record. This limits assessment of how unavailable Week 24 results affected the endpoint and whether alternative missing-data assumptions were examined. The record also does not report a full participant-flow account or sensitivity analyses.

The registry lists multiple outcome measures but does not report a multiplicity strategy or a hierarchy for interpreting secondary endpoints. This restricts the strength of conclusions that can be drawn from secondary comparisons. Full analysis specifications, including any covariate adjustment or other model details, are not reported in the registry record.

The study was open label, so masking was absent. The record does not report further details about outcome assessment procedures. The delayed-switch group could change treatment at Week 24, which means the Week 48 comparison reflects a different treatment history from the primary comparison. Safety summaries separate the delayed-switch period before and after Week 24, but the registry record does not provide death counts or enough information to support causal attribution of adverse events.

These limitations concern what can be concluded from the registry record; they do not establish that unreported procedures were absent from the full study documentation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate Switching From Regimens Consisting of a Ritonavir-boosted Protease Inhibitor (PI) and Two Nucleoside Reverse Transcriptase Inhibitors (NRTIs) to a Fixed-dose Tablet Containing Emtricitabine/Rilpivirine/Tenofovir DF — NCT01252940.
• Registry record last updated 2015-12-04; status last verified 2015-10.
• Results first posted 2013-04-19.
• 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

NCT01252940 is a completed, randomized, open-label, parallel-group Phase 3 study of switching virologically suppressed participants with HIV-1 from a ritonavir-boosted PI and two NRTIs to fixed-dose FTC/RPV/TDF. The study enrolled 482 participants and compared immediate switching with staying on baseline treatment through Week 24, after which the delayed-switch group could switch.

The primary endpoint was the percentage with HIV-1 RNA < 50 copies/mL at Week 24 under the FDA snapshot analysis. The registry reports a sponsor analysis labelled noninferiority or equivalence and also supports an unadjusted recalculation of the primary group contrast. The sponsor margin and complete statistical plan are not reported in the registry record. Secondary outcomes and safety summaries add context, but their interpretation is limited by unreported multiplicity and missing-data details.