D/C/F/TAF Versus COBI-boosted DRV Plus FTC/TDF in HIV-1 Infected, Antiretroviral Treatment Naive Adults: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for D/C/F/TAF Versus COBI-boosted DRV Plus FTC/TDF in HIV-1 Infected, Antiretroviral Treatment Naive Adults (NCT01565850), a randomized phase 2 study. The primary outcome is Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 24.

2. Clinical Question

The clinical question is a comparison of two antiretroviral regimens in people beginning treatment, not a comparison with no treatment. The primary outcome records whether viral RNA was below the stated threshold at a defined follow-up point. It does not, by itself, describe every aspect of safety, tolerability, or longer-term clinical outcomes.

The intervention packages differ in the medicines used and how they are administered: one arm received a single fixed-dose combination tablet, while the other received separate darunavir and cobicistat tablets alongside an emtricitabine/tenofovir disoproxil fumarate fixed-dose tablet. Placebos were included in the arm descriptions. The record therefore describes a blinded comparison of treatment strategies, rather than an isolated test of one ingredient.

3. Trial Design

The registry identifies this as a Phase 2, randomized, double-blinded, parallel-group study. Enrollment was 153. The condition terms include HIV infections and acquired immunodeficiency syndrome. The sponsor was Gilead Sciences. The record gives a study start of 2012-04, primary completion of 2013-01, and status of completed.

Randomization assigns participants to study groups by chance, which is intended to reduce systematic differences between groups at entry. Double masking means participants and relevant study personnel were not meant to know which assigned regimen was being received; the registry record does not specify all roles that were masked. A parallel design means participants were assigned to a treatment group rather than crossing between regimens as part of the stated design.

The D/C/F/TAF arm received the fixed-dose combination tablet with placebo versions of the comparator medicines. The DRV+COBI+FTC/TDF arm received darunavir, cobicistat, and an emtricitabine/tenofovir disoproxil fumarate fixed-dose tablet, with D/C/F/TAF placebo. This matching-placebo description is consistent with the record's double-blind designation.

The registry lists the primary outcome at Week 24 and secondary outcomes at Week 48 and for changes in HIV-1 RNA and CD4+ cell count. The original sample-size justification, intended recruitment targets by arm, allocation ratio as planned, and detailed conduct of randomization are not reported in the registry record. Neither is a full protocol description of follow-up, adherence assessment, or all eligibility criteria. The observed group sizes in outcome analyses should not be mistaken for a complete account of those original design decisions.

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: 232 participants were screened.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set: participant who were randomized;enrolled 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, measured over Week 24.

The primary endpoint is the percentage of participants with HIV-1 RNA < 50 copies/mL at Week 24. It summarizes whether each participant met a prespecified viral-load threshold at the endpoint visit, then expresses the result as a group proportion. The registry describes use of a snapshot algorithm: response status depends on viral load at the predefined time point within an allowed window, together with study-drug discontinuation status.

A threshold-based endpoint is useful because it turns a laboratory measurement into a clinically interpretable response classification at a stated follow-up time. It gives a direct comparison of the proportion meeting the target in each randomized group. It is different from comparing average changes in viral load: a participant just above the threshold and one far above it are both classified as not meeting the endpoint, while the continuous change outcomes preserve more of the numerical information.

The endpoint also has limits. A snapshot classification represents status at the defined time point and incorporates discontinuation, but it does not by itself describe the path of viral load between visits or the reason for a participant's status. The registry's definition does not give the full rules for every possible missing measurement or discontinuation scenario. Those details are not reported in the registry record. Interpretation should therefore remain tied to the stated threshold, time point, and snapshot definition.

7. Results Posted in the Registry

• DRV+COBI+FTC/TDF: 74.0% (37/50) versus 74.8% (77/103) on control; risk difference -0.8 percentage points (95% CI -15.5 to 14.0), risk ratio 0.99 (0.81–1.21); unadjusted two-proportion z-test p = 0.920.

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

• 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:
  • DRV+COBI+FTC/TDF: 84.0% (42/50) versus 76.7% (79/103) on control; risk difference 7.3 percentage points (95% CI -5.7 to 20.3), risk ratio 1.10 (0.93–1.29); unadjusted two-proportion z-test p = 0.298.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DRV+COBI+FTC/TDF and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in HIV-1 RNA at 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:
  • DRV+COBI+FTC/TDF: mean -3.18 versus -3.20 on control; difference 0.02 (95% CI -0.16 to 0.20), standardized effect d = 0.03; z-test p = 0.826.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DRV+COBI+FTC/TDF and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in HIV-1 RNA 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 deviations.
• Result:
  • DRV+COBI+FTC/TDF: mean -3.26 versus -3.27 on control; difference 0.01 (95% CI -0.19 to 0.21), standardized effect d = 0.02; z-test p = 0.923.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DRV+COBI+FTC/TDF and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the comparison beyond the Week 24 threshold result. The registry names Week 48 viral-load response, changes in HIV-1 RNA at follow-up, and changes in CD4+ cell count at follow-up. Taken together, the posted viral-load outcomes do not establish a clear, precise separation between regimens: the Week 48 response comparison has uncertainty spanning no difference, and the continuous HIV-1 RNA comparisons are close in their reported group means with intervals spanning no difference. CD4+ cell count results are not reported in the registry record.

These secondary results provide context for the primary endpoint by examining response at another time point and by using continuous measures rather than only a threshold classification. They do not replace the primary Week 24 comparison. Nor does a broadly similar pattern across reported endpoints prove equivalence: estimates may be imprecise, outcomes address different quantities, and unreported results cannot be assumed to match the visible pattern.

Secondary outcomes generally carry less confirmatory weight when many outcomes are tested and no multiplicity procedure is reported. Repeated testing can increase the chance of at least one apparently notable result arising by chance. The registry does not report whether multiplicity was controlled, whether a hierarchy of endpoints was prespecified, or how the secondary analyses were prioritized. Their p-values and estimates are therefore best treated as supportive or exploratory evidence rather than as independent confirmation of the primary result.

The record lists six outcome measures and six analyses, but the full set of secondary results is not available in the record summarized for these outcomes. In particular, the CD4+ results are absent. Conclusions about the total secondary-outcome pattern should be limited to the outcomes with posted results and should not imply that all planned or measured outcomes are represented.

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
• Change From Baseline in HIV-1 RNA at Week 24
• Change From Baseline in HIV-1 RNA at Week 48
• Change From Baseline in CD4+ Cell Count at Week 24
• Change From Baseline in CD4+ Cell Count at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant is classified according to whether the Week 24 viral-load threshold was met under the snapshot algorithm. Group results are expressed as percentages, and a difference in proportions compares the groups on that scale. This makes the estimate relatively direct to interpret, but its meaning depends on which group is subtracted from which. The sponsor-reported and recalculated differences use methods and reported scales that should not be assumed to be interchangeable.

What does the sponsor's comparison do?

The registry reports a Cochran-Mantel-Haenszel analysis for the primary endpoint. In general, this method can combine comparisons across strata while accounting for the stratification structure used in an analysis. The registry does not report the strata or the complete analysis specification, so the role of any stratification cannot be described further. The sponsor reports a difference in proportions, a confidence interval, and a p-value. Those results represent the trial's own posted analysis and are the principal source for what the registry reports as the sponsor comparison.

What does the recalculation represent?

The recalculated estimates are simple, unadjusted comparisons based on posted group-level summaries. For the primary binary endpoint, the recalculation estimates a risk difference and its interval from the proportions. It does not account for any stratification or other possible features of the sponsor's analysis. It also does not use individual-level data. Consequently, its estimate, interval, and p-value can differ from the sponsor's result without either calculation necessarily being a transcription error. The registry record does not provide enough analytic detail to reconcile every difference between methods.

How should a p-value be read?

A p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. A larger p-value is not evidence that the groups are identical. Interpretation needs the estimated effect and confidence interval alongside the p-value, as well as the design and analysis plan.

The sponsor's primary p-value is 0.64, while the unadjusted recalculation gives p = 0.92. Both are above common thresholds for statistical significance, but that observation alone does not establish equivalence or non-inferiority. In particular, a formal non-inferiority conclusion depends on a prespecified margin and a suitable analysis framework. The registry record does not report the margin or the full decision rules. The classification of the analysis as non-inferiority or equivalence should therefore not be expanded into an unsupported claim about the conclusion.

Why are confidence intervals useful?

A confidence interval gives a range of effect estimates compatible with the observed data and the method's assumptions at the stated confidence level. It communicates uncertainty in the estimate, not a guarantee that the true effect lies in the interval. For a difference, an interval that crosses zero includes no difference as one possibility, while also potentially allowing differences in either direction. The width conveys how precisely the effect has been estimated.

For continuous outcomes, the registry reports changes from baseline as means with standard deviations and sponsor comparisons using analysis of variance (ANOVA), with differences in least-squares means. In general, ANOVA compares group means under a model, and a least-squares mean is a model-based group estimate. The registry does not describe the full ANOVA model or its covariates. The recalculated comparisons use posted means and standard deviations and are unadjusted; they are not a substitute for the sponsor's model-based estimates.

Binary and continuous outcomes answer different questions. The viral-load threshold outcome asks whether participants met a defined status at a time point. Mean change in HIV-1 RNA describes the average change on the continuous log10 copies/mL scale. CD4+ cell count outcomes describe another measure, but their posted results are absent. The endpoints should not be treated as duplicate tests of exactly the same quantity.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variability is greater than a statistical model expects. If it is ignored, standard errors may be too small and intervals may appear too narrow. It is more relevant to some count or clustered-data settings than to a simple comparison of proportions or means. The primary endpoint is a binary percentage, and the posted continuous outcomes include standard deviations. The registry does not report an over-dispersion model for these analyses, so none should be inferred.

The registry reports six outcome measures and six analyses overall, while naming a broader set of secondary outcome types. It does not report a complete statistical analysis plan, whether interim analyses occurred, or how multiplicity was handled. Those absences limit assessment of which analyses were prespecified, how the sponsor selected its model, and how much weight to give results across multiple endpoints. General statistical principles can explain these issues, but cannot replace missing trial-specific details.

11. Confidence Intervals and Precision

Precision is reflected in the range of values compatible with the data under a stated analysis, not just in the point estimate. For the Week 24 primary sponsor comparison, the reported 95% confidence interval is from -11.4 to 18.1 around a difference in proportions of 3.3. The interval spans zero and extends to differences in either direction. It therefore leaves substantial uncertainty about the size and direction of the contrast.

The unadjusted recalculation has a risk-difference estimate of -0.008 and a 95% confidence interval from -0.155 to 0.140. It too spans zero and permits a range of possible effects. These are not identical summaries: the sponsor used a Cochran-Mantel-Haenszel method, while the recalculation is unadjusted. The interval width should be interpreted in relation to the method that produced it, and the sponsor result remains the trial's reported analysis.

Confidence intervals are not probability statements about the true effect. A 95% interval is a procedure that, under its assumptions, would cover the true value in 95% of repeated applications. For this particular study, the interval is one estimate of uncertainty. It does not show that every value inside is equally plausible, and values outside are not logically impossible.

The number of participants contributing to an outcome, the variability of the outcome, and the analysis method all influence precision. The posted outcome groups have different sizes, and the continuous endpoints have reported standard deviations. No new precision calculation is needed to see the main limitation: the primary interval is broad relative to its estimate and does not narrow the plausible contrast to one direction. Precision also differs by endpoint and follow-up time, so one result should not be used as a proxy for all outcomes.

For non-inferiority or equivalence questions, precision must be judged against a prespecified margin, not only against zero. That margin and the detailed decision criteria are not reported in the registry record. The confidence interval alone therefore cannot establish that the regimens meet a particular non-inferiority or equivalence standard.

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 values are illustrations based on the observed effects, not the original design calculation. For these non-time-to-event outcomes, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The illustrated effect to detect is the stated fraction of the observed effect. The original design assumptions are not reported in the registry record.

The 80% power column gives the approximate participants per arm that the planning calculation would require to have an 80% chance of detecting the specified effect under those assumptions, if that effect and model were correct. The 90% power column gives the corresponding planning number for a higher target chance of detecting that effect. These are design illustrations, not descriptions of what happened in the completed trial.

Rows for 100%, 75%, and 50% of the observed effect show how the planning requirement changes when the target effect is reduced. Smaller effects are harder to distinguish from random variation and therefore require more participants. This relationship applies to the planning calculations; it does not show that the trial was adequately or inadequately powered for its original objectives.

The planning display is not observed power. Observed power is not a useful substitute for reading the estimated effect and its confidence interval after a study has been completed. Here, the planning figures answer a hypothetical design question under stated assumptions. They do not revise the trial's results, and they cannot establish what sample size the investigators originally intended, because that justification 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 = 0.748; treatment proportion p₁ = 0.740; average p̄ = 0.744.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6174 = 1.2100.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6173 = 0.5196.
4. n = (1.2100 + 0.5196)² / (-0.0076)² = 52,163.1, rounded up to 52,164 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 <- 0.747572815533981                          # control proportion
p1 <- 0.74                          # 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(1565850)
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 = 52,164 (80% power), 69,832 (90% power)
 75% of observed effect: n per arm = 92,511 (80% power), 123,845 (90% power)
 50% of observed effect: n per arm = 207,642 (80% power), 277,973 (90% power)
power.prop.test: 52163.1 
Simulated power at n = 52,164 per arm: 0.805 (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's own primary analysis is a Cochran-Mantel-Haenszel comparison of proportions. It reports a difference of 3.3, a 95% confidence interval from -11.4 to 18.1, and p = 0.64. That is the sponsor's reported analysis and should be distinguished from the simple unadjusted recalculation, which gives a risk difference of -0.008, a 95% confidence interval from -0.155 to 0.140, and p = 0.92.

The calculations are not identical in method or reported scale. The recalculation uses only the posted group-level proportions and does not reproduce the Cochran-Mantel-Haenszel analysis. The record does not contain enough detail about the sponsor's analysis specification to explain every difference. Their estimates should not be combined or treated as though they came from the same model.

The sponsor result is the trial's reported inferential analysis; the recalculation is a transparent check based on summary statistics. Neither should be described as proving the regimens are equal. The confidence intervals and the missing non-inferiority margin constrain what can be concluded. The registry record reports no discrepancy flag, but that does not eliminate the methodological distinction between the sponsor analysis and the unadjusted calculation.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one endpoint, time point, or comparison. Even if each test is interpreted using its own significance threshold, performing many tests increases the chance that at least one result appears statistically notable by chance. This is a general statistical issue, not evidence that any particular finding in this trial is false.

The registry names a primary Week 24 viral-load response outcome and several secondary outcomes, including Week 48 response and changes in HIV-1 RNA and CD4+ cell count. It does not report a multiplicity adjustment, a formal testing hierarchy, or the complete statistical analysis plan. It is therefore not possible to determine from the registry record whether the secondary tests were intended as confirmatory, how family-wise error was handled, or whether analyses were selected before results were known. Unadjusted secondary results should be interpreted cautiously.

The primary outcome population is described as the Full Analysis Set: participants who were randomized, enrolled, and received at least one dose of study drug. That definition identifies the population used for the primary outcome, but the registry does not provide a detailed account of exclusions, missing Week 24 measurements, or the number classified as failures under every snapshot scenario. The snapshot algorithm incorporates viral load within an allowed time window and study-drug discontinuation status. The complete rules for missing data and discontinuation are not reported in the registry record.

For secondary outcomes, the number contributing can differ by measure and follow-up, as reflected in the posted outcome summaries. The record does not describe all reasons for missing observations or the assumptions used to handle them. Missing data can affect both the estimated result and the uncertainty around it, especially if the chance of missingness differs between groups or is related to outcome status.

The original sample-size justification, interim-analysis plan, and detailed analysis plan are not reported in the registry record. Their absence means that the reported p-values and intervals can be described, but cannot be fully evaluated against every intended design decision. This uncertainty supports a restrained reading of secondary findings and of any non-inferiority or equivalence interpretation.

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: bronchitis (2.0%), bronchitis viral (2.0%), pneumonia (2.0%), renal tubular disorder (2.0%), diarrhoea haemorrhagic (1.0%).

The registry lists serious adverse events affecting 5 of 103 participants in the D/C/F/TAF group and 2 of 50 in the DRV+COBI+FTC/TDF group. It lists other adverse events affecting 77 of 103 and 40 of 50, respectively. These counts describe the posted safety summaries; they do not by themselves establish that an event was caused by a study medicine or compare the severity, duration, or clinical importance of all events.

The serious-event terms listed include Bronchitis, Bronchitis viral, Pneumonia, and Renal tubular disorder, each reported as 2.0%, and Diarrhoea haemorrhagic and Hypersensitivity, each reported as 1.0%. The record does not assign these listed terms to a particular arm in the summary. The death figures are not reported in the registry record.

Safety counts should be read alongside the study's size, follow-up, event definitions, and the completeness of reporting. The registry does not provide enough detail to assess exposure-adjusted rates or make causal comparisons. These figures are descriptive and do not establish that either regimen is safer.

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

The posted data describe a randomized comparison of two antiretroviral regimens in treatment-naive adults with HIV-1. For the primary Week 24 endpoint, the observed response percentages are close, and the sponsor's confidence interval includes no difference while also allowing differences in either direction. The unadjusted recalculation leads to the same broad caution about uncertainty, though it is not the sponsor's method.

This result does not establish that the regimens are identical. It also does not demonstrate a clinically important advantage for either regimen. A failure to find a statistically significant difference is not proof of no effect, and an analysis labelled non-inferiority or equivalence cannot be interpreted formally without the margin and decision criteria. Those details are not reported in the registry record.

The result is limited to the stated population, regimen comparison, outcome definitions, and follow-up periods. The primary endpoint is a snapshot response status at Week 24, not a complete account of treatment experience over time. Secondary outcomes add information about later response and laboratory changes, but their results are not all reported and multiplicity handling is not stated. The record does not support claims about outcomes beyond those measured and posted.

The safety summaries list serious and other adverse events, but counts alone do not establish causation or comparative safety. Likewise, the sample-size illustrations are hypothetical planning calculations, not evidence about the trial's achieved power. The trial's original design assumptions and sample-size justification are not reported in the registry record.

Overall, the evidence in the record is compatible with no clear separation in the reported efficacy comparisons, but the precision does not rule out differences. The appropriate reading is descriptive and bounded: it reflects the reported estimates and their uncertainty, rather than a universal conclusion about all patients, treatment settings, or longer-term outcomes.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical comparison should be read through its estimand, analysis method, and uncertainty rather than through the two response percentages alone. The primary endpoint is a threshold-based snapshot that incorporates both viral-load status and treatment discontinuation. That definition determines what counts as response and makes the result different from a comparison of average viral-load change.

It also illustrates the distinction between a sponsor's reported analysis and a simple recalculation from group summaries. The sponsor used a Cochran-Mantel-Haenszel method, while the recalculation is unadjusted. They answer related questions but are not interchangeable. Reporting both estimates can help readers understand how a summary-data comparison behaves, while preserving the sponsor analysis as the trial's own inferential result.

The interval matters because the estimates are uncertain. A non-significant test does not prove equality, and a formal non-inferiority interpretation requires a prespecified margin. The registry record does not report that margin. This is a practical example of why labels, p-values, and close point estimates cannot replace a full account of the intended decision rule.

The trial also shows the importance of endpoint completeness and multiplicity reporting. Several secondary outcome types are named, but CD4+ results are not reported in the registry record, and multiplicity handling is not stated. Without those details, the secondary evidence is informative but limited in confirmatory force.

Finally, planning illustrations based on observed effects answer a different question from the trial's actual design. They can show how assumptions about effect size and power change planning requirements, but they cannot reveal the original rationale or establish observed power. Keeping those statistical questions separate supports a more careful reading of clinical trial records.

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 record does not report the original sample-size justification or the planned design assumptions, so the observed enrollment cannot be evaluated against the investigators' original power target. The planning illustrations based on observed effects are not a replacement for that missing information.

The sponsor's primary analysis is reported as a Cochran-Mantel-Haenszel comparison, but the registry does not provide the complete analysis specification or the strata used. The unadjusted recalculation uses summary statistics and cannot reproduce an analysis based on additional structure or participant-level information. This limits direct comparison of their estimates.

The registry labels the primary analysis as non-inferiority or equivalence type, but does not report the margin, detailed decision criteria, or full protocol. A formal conclusion on either basis cannot be independently assessed from the posted record alone. The registry also does not report whether interim analyses took place or describe a complete statistical analysis plan.

The primary endpoint uses a snapshot algorithm, but the complete rules for missing measurements and discontinuations are not available. The Full Analysis Set definition is reported, yet detailed information about missing observations and exclusions is not. This constrains assessment of possible missing-data effects.

Some secondary outcome results are not reported, including the named CD4+ cell count outcomes. The record does not state how multiplicity was handled, limiting the confirmatory interpretation of the available secondary findings. The posted safety summaries are descriptive and do not provide the detail needed to establish causality or fully compare risk over time. These limitations apply to interpretation of the registry record and do not, by themselves, show that the study was improperly conducted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: D/C/F/TAF Versus COBI-boosted DRV Plus FTC/TDF in HIV-1 Infected, Antiretroviral Treatment Naive Adults — NCT01565850.
• Registry record last updated 2016-04-11; status last verified 2016-03.
• Results first posted 2016-04-11.
• 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

NCT01565850 is a completed Phase 2 randomized, double-blinded, parallel-group study sponsored by Gilead Sciences. It compared D/C/F/TAF with DRV+COBI+FTC/TDF in antiretroviral treatment-naive adults with HIV-1. Enrollment was 153; the record gives a study start of 2012-04 and primary completion of 2013-01.

The primary outcome was the percentage with HIV-1 RNA < 50 copies/mL at Week 24, assessed using a snapshot algorithm in the Full Analysis Set. The sponsor reported a Cochran-Mantel-Haenszel difference in proportions with a 95% confidence interval spanning no difference. The unadjusted recalculation is a separate summary-data analysis and should not be treated as the sponsor result.

Posted secondary viral-load results do not establish a clear separation between groups; CD4+ cell count results are not reported in the registry record. The registry lists serious and other adverse-event counts but does not report deaths in the posted summary. The original sample-size justification, full multiplicity plan, and detailed non-inferiority margin are not reported in the registry record.