A Trial Comparing GSK1349572 50mg Once Daily to Raltegravir 400mg Twice Daily: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Trial Comparing GSK1349572 50mg Once Daily to Raltegravir 400mg Twice Daily (NCT01227824), a randomized phase 3 study. The primary outcome is Percentage of Participants With Human Immunodeficiency Virus-1 (HIV-1) Ribonucleic Acid (RNA) [HIV-1RNA] <50 Copies (c)/Milliliter (mL) Through Week 48.

2. Clinical Question

The question is about a defined virologic outcome under a specified analysis rule, not simply whether participants had any HIV-1 RNA result at a particular visit. Missing results and some treatment changes are counted as failures under the snapshot approach, so the endpoint incorporates both the measured viral-load outcome and the analysis rule for participants whose treatment or available data do not follow the intended assessment path.

The registry describes the study as involving antiretroviral therapy-naive adults with HIV-1 infection. Both groups received background NRTI therapy; the contrast was between the two study-drug regimens, with placebos used to support masking of the different dosing schedules. The primary endpoint concerns response through Week 48, while the trial description also says non-inferiority would be tested at Week 96. The posted primary result is the Week 48 result.

3. Trial Design

The registry identifies this as a randomized, parallel-group Phase 3 study, with quadruple masking. Its official title describes it as double blind. The record does not explain which people or roles were included in the quadruple-masking classification. The study is marked completed. Its recorded enrollment is 828, and the primary analysis includes 411 participants in each treatment group.

One group received GSK1349572 50 mg once daily, identified elsewhere in the record as dolutegravir, together with raltegravir placebo twice daily and background NRTI therapy once daily. The other received raltegravir 400 mg twice daily, GSK1349572 placebo once daily, and background NRTI therapy once daily. The stated background options were ABC/3TC or TDF/FTC. This double-dummy arrangement is consistent with the listed schedules, but further implementation details are not reported in the registry record.

The brief description frames the study as an assessment of non-inferior antiviral activity through 48 weeks and says non-inferiority would also be tested at Week 96. The primary endpoint is the percentage with HIV-1 RNA below 50 copies/mL through Week 48. A Week 96 secondary outcome also concerns the number of participants below that viral-load threshold. The record lists additional secondary outcomes covering viral-load measures, CD4+ cell counts, integrase inhibitor resistance, and HIV-associated conditions and progression.

The study start is recorded as 2010-10-19 and primary completion as 2012-02-06. These are registry dates, not a description of each participant’s follow-up. The original sample-size justification, the planned non-inferiority margin, detailed randomization procedures, and details of any interim analyses 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: Total 1035 participants were screened; 827 participants were randomized, and 822 participants entered the treatment period. Of the 5 participants who were randomized but not treated with investigational product, 4 withdrew consent and 1 was randomized in error. 338 participants were enrolled in open label phase to receive Dolutegravir.

Double-blind Phase: 96 Weeks Duration

Reasons for not completing this period:

Open-label Phase: Median of 1267 Days

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT-E Population.

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 Human Immunodeficiency Virus-1 (HIV-1) Ribonucleic Acid (RNA) [HIV-1RNA] <50 Copies (c)/Milliliter (mL) Through Week 48, measured over Baseline up to Week 48.

The primary endpoint is the percentage of participants with plasma HIV-1 RNA below 50 copies/mL through Week 48. Viral RNA is a measure of circulating HIV-1, and the threshold defines the response being counted. The endpoint is binary at the participant level: a participant is classified as meeting or not meeting the response definition under the analysis rule.

The registry specifies the Missing, Switch or Discontinuation = Failure snapshot algorithm. Participants without HIV-1 RNA data are treated as non-responders. Treatment switching is also handled according to the study’s rules for background ART substitutions: the record distinguishes substitutions that were not permitted from those permitted under the study, and describes an exception based on whether a decision to switch had been documented by the first on-treatment visit with an RNA assessment. Otherwise, the last available on-treatment HIV-1 RNA assessment determines virologic success or failure.

This kind of endpoint is used to summarize the proportion meeting a clinically defined laboratory threshold while accounting for missing assessments and treatment changes through a prespecified classification approach. It is therefore not identical to a comparison limited to participants with an observed viral-load measurement at the target time. The primary population is ITT-E, defined in the registry as randomized participants who received at least one dose of study medication.

The registry record does not report the non-inferiority margin or a fuller account of how the endpoint definition was selected. Those details matter when interpreting a non-inferiority claim, because the result must be assessed against the planned margin and the specified analysis strategy.

7. Results Posted in the Registry

• RTG 400 mg BID: 84.9% (349/411) versus 88.1% (362/411) on control; risk difference -3.2 percentage points (95% CI -7.8 to 1.5), risk ratio 0.96 (0.91–1.02); unadjusted two-proportion z-test p = 0.185.

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 Plasma HIV-1 RNA <50 c/mL

• 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:
  • RTG 400 mg BID: 76.4% (314/411) versus 80.8% (332/411) on control; risk difference -4.4 percentage points (95% CI -10.0 to 1.2), risk ratio 0.95 (0.88–1.02); unadjusted two-proportion z-test p = 0.126.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RTG 400 mg BID and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 11 secondary outcomes, covering virologic response and change over time, CD4+ cell counts, integrase inhibitor resistance, and HIV-associated conditions and progression. The numerical secondary-result data available in the record include the Week 96 count of participants with HIV-1 RNA below 50 copies/mL. That result follows the same broad direction as the Week 48 primary arm percentages, but it is a separate endpoint at a later time point and should be interpreted as supportive context rather than as a replacement primary result.

The other listed secondary outcomes do not have corresponding numerical results in the record summarized for this analysis. Their absence means that the overall pattern across all secondary outcomes cannot be assessed from the posted numerical results. It is not possible to infer unreported results from the outcome names or from the primary endpoint.

Secondary outcomes commonly broaden the view of a trial, but each additional analysis creates more opportunities for chance findings when many hypotheses are examined. In general, multiplicity procedures can control the overall false-positive risk or otherwise define which analyses are confirmatory. The registry record does not report a multiplicity adjustment or a hierarchy for secondary hypotheses. Accordingly, unadjusted secondary findings, where available, carry less confirmatory weight than a prespecified primary analysis and should be interpreted cautiously.

The secondary outcome categories also differ in meaning and statistical structure. A binary threshold response is not interchangeable with a change in viral load, a CD4+ cell count, a resistance finding, or a clinical progression outcome. The registry’s listed outcomes indicate what was intended to be assessed; they do not establish the result for outcomes without posted numerical data.

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

• Number of Participants With Detectable HIV-1 Virus That Has Genotypic or Phenotypic Evidence of INI Resistance.
• Number of Participants With Plasma HIV-1 RNA <50 c/mL
• Number of Participants With Plasma HIV-1 RNA <400 c/mL
• Change From Baseline in Plasma HIV-1 RNA Over Time
• Absolute Values in Plasma HIV-1 RNA Over Time
• Change From Baseline in Cluster of Differentiation (CD)4+ Cell Counts Over Time
• Absolute Values in CD4+ Cell Counts Over Time
• Number of Participants With the Indicated Post-Baseline HIV-associated Conditions and Progression, Excluding Recurrences

9. Statistical Interpretation

10. Statistical Methods Explained

What kind of outcome is being analyzed?

The primary outcome is binary at the participant level: each person is classified according to whether HIV-1 RNA is below 50 copies/mL through Week 48 under the stated snapshot rule. The arm-level result is presented as a percentage of participants. This makes the primary comparison a comparison of response proportions rather than a comparison of average viral-load values. The registry also lists continuous-style viral-load and CD4+ outcomes, but those are not the primary endpoint described in this result.

For a binary outcome, the analysis can describe each group’s response proportion and compare those proportions using a difference, a ratio of risks, or a ratio of odds. These measures answer related but distinct questions. A risk difference expresses an absolute contrast in proportions; a risk ratio compares proportions relative to one another; an odds ratio compares odds. The registry’s sponsor result is labelled as a difference in percentage. The recalculated summary includes other effect measures, but the sponsor’s analysis method is not reported in the registry record.

What does the snapshot rule do?

The Missing, Switch or Discontinuation = Failure approach assigns non-response to participants without HIV-1 RNA data. It also includes rules for certain changes to concomitant ART. This prevents the primary response percentage from being calculated solely among participants with an observed measurement and uninterrupted treatment. Such rules can make the endpoint more representative of the treatment strategy as implemented under the protocol, but they also mean that a response percentage depends on both the laboratory threshold and the classification rules.

In general, outcome handling can affect a treatment comparison if missingness, treatment changes, or discontinuations differ between groups. The registry describes the broad endpoint algorithm but does not provide the participant-level missingness pattern or the number classified as failures for each reason. The posted aggregate results cannot separate the contribution of measured viral-load response from the contribution of missing-data and switching rules.

What is the role of the analysis population?

The stated primary population is ITT-E: all randomized participants who received at least one dose of study medication. This definition retains participants according to their randomized group after exposure, rather than restricting the primary population to people who completed treatment or had a complete endpoint measurement. The record gives 411 participants per group for the primary result. It also reports total enrollment of 828; the registry does not explain the difference between total enrollment and the number in each posted primary arm.

In general, analysis populations should be interpreted in light of the question they are intended to answer and the handling of participants who deviate from assigned treatment. The endpoint’s failure rules are particularly relevant because they specify how some absent measurements and treatment changes enter the response classification. Additional analysis populations and sensitivity analyses are not reported in the registry record.

How should the non-inferiority result be approached?

A non-inferiority analysis asks whether the comparative result is sufficiently compatible with the new regimen being no worse than the comparator by more than a prespecified margin. The margin is essential: it defines the largest loss that the trial plan would accept for the endpoint. The registry reports the sponsor’s difference and confidence interval but does not report the margin, the rationale for selecting it, or the sponsor’s statistical method. The result therefore cannot be independently checked against the planned decision threshold from the registry record alone.

In general, a confidence interval is a range of values that reflects the uncertainty in an estimate under a specified statistical model and procedure. In a non-inferiority setting, a confidence interval is not interpreted only by asking whether it contains zero. Its position relative to the non-inferiority margin is central. Without the margin and full analysis details, the posted result should be described as the reported estimate and interval rather than as an independently verified conclusion about the formal criterion.

What does the recalculation represent?

The recalculated statistics are simple, unadjusted calculations based on the posted arm summaries. They do not reproduce the sponsor’s analysis unless the calculation method, analysis population, endpoint classification, and group ordering match. The recalculated p-value is 0.185. A p-value is a measure of how incompatible the observed data are with a specified null model, assuming that model and the analysis are appropriate; it is not the probability that the null hypothesis is true, nor is it a measure of clinical importance.

For the primary comparison, the recalculation is oriented as RTG relative to DTG, whereas the sponsor’s reported difference is ordered DTG then RTG. A reversal in group order reverses the sign of a difference while preserving the underlying contrast. Beyond orientation, the registry does not state why the recalculation and sponsor presentation may differ in their numerical form. The recalculation should therefore be treated as a transparent descriptive cross-check, not as a replacement for the registry-reported non-inferiority analysis.

In general, a nonsignificant unadjusted test does not prove equality, and a significant test would not by itself establish non-inferiority. Non-inferiority requires a prespecified margin and a design and analysis suited to that question. These concepts are general statistical explanations; the registry does not provide all the trial-specific details needed to assess every assumption.

11. Confidence Intervals and Precision

The sponsor-reported primary difference is 2.5, with a 95% confidence interval from -2.2 to 7.1. The interval spans zero and includes values on either side of no difference. It therefore conveys uncertainty about the direction and size of the group contrast under the sponsor’s analysis. The registry does not report a p-value for this analysis.

In general, a confidence interval is not a guarantee that the true effect lies within its endpoints. It describes the range of estimates compatible with the observed data and the method’s assumptions at the stated confidence level. A wider interval indicates less precision than a narrower interval, all else being equal. The interval’s clinical or non-inferiority interpretation also depends on the prespecified margin, which is not reported in the registry record.

The arm-level percentages are 88.0% and 85.0%, with 411 participants in each group. The recalculated unadjusted analysis has an interval that includes zero as well. Because that calculation is not the sponsor’s analysis and uses the opposite group ordering for the risk difference, it should not be conflated with the sponsor-reported 95% interval.

Precision depends on the amount of information in the analysis, the outcome frequency, and the analysis method. General statistical reasoning would expect more information to narrow uncertainty, but no additional precision estimate should be inferred from the registry’s enrollment figure alone. The record does not provide the planned margin, original sample-size justification, or detailed modeling approach. Those omissions limit assessment of whether the achieved precision was adequate for the trial’s stated non-inferiority objective.

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 figures are illustrations based on the observed effect, not the trial’s original design calculation. For the binary outcomes in these calculations, the figures are participants per arm, not total participants and not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the estimated participants per arm for a hypothetical study to have an 80% chance of detecting the selected effect under those assumptions, if that effect and the model assumptions were correct. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are design illustrations, not evidence that a result from this trial had a particular probability of being significant.

The rows consider planning for 100%, 75%, and 50% of the observed effect. In general, planning for a smaller effect requires more participants, because a smaller contrast is harder to distinguish from random variation. For the primary endpoint, the listed per-arm figures are 1,832 and 2,452 for planning at 100% of the observed effect; 3,176 and 4,252 for 75%; and 6,964 and 9,322 for 50%, for 80% and 90% power respectively. These are hypothetical future planning values, not a description of the enrolled trial’s power.

For the Week 96 secondary binary outcome, the corresponding per-arm figures are 1,376 and 1,842 for 100% of the observed effect; 2,402 and 3,214 for 75%; and 5,299 and 7,093 for 50%. They use the same stated planning assumptions, but are based on that outcome’s observed effect and should not be substituted for the primary endpoint’s planning illustration.

These calculations are not observed power. The trial’s own original sample-size assumptions and justification are not reported in the registry record. The planning figures also do not establish that the original design was powered for the observed effect, or that the formal non-inferiority objective was met.

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 = 0.881; treatment proportion p₁ = 0.849; average p̄ = 0.865.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4833 = 0.9473.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4828 = 0.4063.
4. n = (0.9473 + 0.4063)² / (-0.0316)² = 1,831.5, rounded up to 1,832 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 <- 0.880778588807786                          # control proportion
p1 <- 0.849148418491484                          # 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(1227824)
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 = 1,832 (80% power), 2,452 (90% power)
 75% of observed effect: n per arm = 3,176 (80% power), 4,252 (90% power)
 50% of observed effect: n per arm = 6,964 (80% power), 9,322 (90% power)
power.prop.test: 1831.5 
Simulated power at n = 1,832 per arm: 0.801 (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 posts a sponsor analysis for the primary outcome as a non-inferiority or equivalence analysis. It gives a difference in percentage of 2.5 and a 95% confidence interval from -2.2 to 7.1, with DTG listed before RTG. That is the sponsor-reported result and should be kept distinct from the simple unadjusted recalculation based on the posted arm counts.

The recalculation uses the opposite group orientation, RTG relative to DTG, and produces an unadjusted p-value of 0.185. A difference changes sign when the order of the groups is reversed. The recalculation is a summary-statistic cross-check, not an attempt to reproduce the sponsor’s method. The registry record does not report the method used for the sponsor analysis, its p-value, or the reason for any difference in numerical presentation.

For a non-inferiority conclusion, the key comparison is between the relevant confidence limit and the planned non-inferiority margin. The margin is not reported in the registry record, so the sponsor’s formal decision cannot be reconstructed from the posted estimate and interval alone. The recalculated p-value addresses a simple unadjusted comparison and is not itself a test of the non-inferiority criterion.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists 11 secondary outcomes. It does not report a hierarchy among the secondary outcomes, a family of confirmatory hypotheses, or a procedure for adjusting inference across multiple analyses. When multiple outcomes are tested, the chance of at least one apparently unusual result can increase if each is assessed without accounting for the others. In general, multiplicity methods address that issue by controlling or otherwise defining the error rate across a set of tests. No trial-specific adjustment should be assumed in the absence of a reported plan.

The record describes the primary outcome’s Missing, Switch or Discontinuation = Failure approach. Participants without HIV-1 RNA data are classified as non-responders, and the description gives rules for certain background ART substitutions. This is important because the primary percentage is not simply a complete-case summary. However, counts of missing measurements, treatment discontinuations, switches, and the reasons for missingness are not reported in the registry record. Nor does the record provide sensitivity analyses showing how alternative assumptions about missing outcomes might affect the result.

The primary population is ITT-E, defined as randomized participants who received at least one dose of study medication. The record does not provide additional analysis-population results that would allow comparison with a per-protocol population or another sensitivity population. In general, non-inferiority assessments can be sensitive to analysis-population choices and missing-data handling; the registry’s endpoint definition alone does not resolve all such concerns.

The formal non-inferiority margin, its justification, the sponsor’s detailed statistical method, and details of interim analyses are not reported in the registry record. Those omissions limit assessment of how the primary analysis was planned and whether the posted result matches the intended decision process. The registry does not report whether multiplicity, missing-data sensitivity, or population sensitivity was addressed in a protocol or statistical analysis plan.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: appendicitis (1.2%), suicide attempt (0.7%), drug hypersensitivity (0.7%), syphilis (0.6%), pneumonia (0.5%).

For the randomized DTG group, the registry reports serious adverse events in 41 of 411 participants; for the randomized RTG group, it reports serious adverse events in 45 of 411 participants. It also records one death in each of those groups. These are counts, not estimates of whether an event was caused by a study drug.

A separate DTG open-label group is listed with 21 serious adverse events among 338 participants and no deaths. This group is distinct from the two randomized groups and should not be treated as an additional randomized comparator. The record does not explain the circumstances or follow-up structure for this open-label group.

The registry also reports other adverse events affecting 353 of 411 participants in the DTG group, 344 of 411 in the RTG group, and 256 of 338 in the open-label DTG group. Serious adverse events are a subset defined by seriousness, and should not be read as equivalent to all reported adverse events. Listed serious-event terms and percentages include appendicitis at 1.2%, suicide attempt at 0.7%, drug hypersensitivity at 0.7%, syphilis at 0.6%, pneumonia at 0.5%, and laceration at 0.5%.

These figures are descriptive registry counts. They do not establish comparative risk, causality, or the full safety profile, and the record does not report event-level timing or adjusted analyses.

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

The primary result describes the proportion of participants classified as having HIV-1 RNA below 50 copies/mL through Week 48 under the registry’s snapshot failure rules. The posted arm percentages and sponsor-reported difference provide a comparative summary, while the confidence interval conveys uncertainty around that difference. The result should be read as an analysis of a defined population and endpoint, not as an unrestricted statement about every person with HIV-1 infection or every treatment setting.

The trial was randomized and compared two regimens, each combined with background NRTI therapy. Its outcome concerns a virologic threshold. It does not directly answer every question about longer-term clinical outcomes, resistance, CD4+ counts, quality of life, or safety. Those topics appear among the listed secondary outcomes, but numerical results are not available for all of them in the registry record.

The record’s stated aim was non-inferiority, but the margin is not reported. The sponsor’s interval is therefore not enough to independently verify whether the planned non-inferiority criterion was met. A general statistical distinction is important: failure to show a conventional difference is not proof that two treatments are equivalent, and a non-inferiority conclusion requires a specified margin and an analysis designed to assess it.

The endpoint counts missing HIV-1 RNA data as failure and applies rules to some treatment changes. This makes the reported response percentage dependent on the endpoint algorithm as well as on measured viral load. The registry does not provide enough detail to isolate those components or assess how alternative missing-data assumptions would change the result.

The findings should not be turned into medical advice or a claim that either regimen works or does not work. They are a statistical description of the posted comparison, with uncertainty and reporting limitations that matter to its interpretation.

18. Why This Trial Matters Statistically

This trial is statistically notable for pairing a stated non-inferiority objective with a binary virologic endpoint and an explicit failure rule for missing data and certain treatment changes. Those choices illustrate why a response percentage is more than a count of observed laboratory results: the analysis definition determines how participants without an eligible measurement enter the comparison.

It also highlights the importance of the non-inferiority margin. A reported estimate and confidence interval can be described without the margin, but the formal non-inferiority interpretation depends on how the interval relates to that prespecified boundary. Since the margin and its rationale are not reported in the registry record, readers cannot fully reconstruct the sponsor’s decision criterion from the posted result alone.

The distinction between the sponsor analysis and an unadjusted recalculation is another useful statistical lesson. Recalculations from arm summaries can serve as checks, but they do not necessarily reproduce the sponsor’s analysis or its estimand. Group ordering, analysis rules, and model choice all matter. A simple p-value should not be mistaken for the trial’s formal non-inferiority test.

Finally, the record shows how secondary outcomes and safety summaries add context without replacing the primary analysis. The registry lists a broad set of secondary questions, but numerical results are not available for all of them in the record. The case therefore underscores the value of complete reporting of analysis methods, missing-data patterns, multiplicity handling, and planned decision criteria.

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 non-inferiority margin, the rationale for that margin, or the original sample-size justification. These are central design details for evaluating a non-inferiority study. The sponsor analysis is labelled as non-inferiority or equivalence, but its statistical method and p-value are not reported, limiting independent reconstruction of the formal analysis.

The primary endpoint description specifies how missing HIV-1 RNA data and certain treatment changes are classified, but the record does not provide counts by missingness reason, treatment change, or failure category. It also does not report sensitivity analyses under alternative missing-data assumptions or results from other analysis populations. These omissions restrict assessment of robustness to endpoint handling.

The record lists 11 secondary outcomes, but numerical results are not available for all those outcomes in the posted data. It does not report a multiplicity strategy or a hierarchy of secondary hypotheses. Consequently, a comprehensive assessment of secondary findings and their confirmatory status is not possible.

The posted enrollment is 828, while the primary analysis lists 411 participants in each group; the registry does not explain the relationship between these figures. The record also includes a DTG open-label safety group, but does not describe its relation to the randomized groups or its follow-up context. These details constrain interpretation of the safety counts.

Details of randomization implementation, the components included in quadruple masking, interim analyses, and the sponsor’s full statistical analysis plan are not reported in the registry record. These are reporting limitations; they do not establish that the procedures were absent, only that they cannot be assessed from this record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Trial Comparing GSK1349572 50mg Once Daily to Raltegravir 400mg Twice Daily — NCT01227824.
• Registry record last updated 2018-10-09; status last verified 2018-10.
• Results first posted 2014-06-23.
• 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

NCT01227824 is a completed randomized, parallel-group Phase 3 trial in antiretroviral therapy-naive adults with HIV-1 infection. It compared GSK1349572, identified as dolutegravir, 50 mg once daily with raltegravir 400 mg twice daily, with both groups receiving background NRTI therapy.

The primary endpoint was the percentage with HIV-1 RNA below 50 copies/mL through Week 48 in the ITT-E population, using a Missing, Switch or Discontinuation = Failure snapshot approach. The sponsor analysis reported a difference in percentage of 2.5 with a 95% confidence interval from -2.2 to 7.1. The non-inferiority margin and detailed sponsor method are not reported in the registry record.

The registry lists 11 secondary outcomes and reports a Week 96 result for the same viral-load threshold, but numerical results are not available for every listed secondary outcome. Safety figures include serious adverse events and deaths in the randomized groups, plus a separate open-label DTG group. Interpretation is limited by missing design and analysis details, including the planned margin, original sample-size justification, and multiplicity procedures.