A Trial Comparing GSK1349572 50mg Plus Abacavir/Lamivudine Once Daily to Atripla (Also Called The SINGLE Trial): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Trial Comparing GSK1349572 50mg Plus Abacavir/Lamivudine Once Daily to Atripla (Also Called The SINGLE Trial) (NCT01263015), a randomized phase 3 study. The primary outcome is Proportion of Subjects Responding Based on Plasma HIV-1 RNA <50 c/mL at Week 48.

2. Clinical Question

The primary outcome is a binary virologic response: each participant is classified as a responder or non-responder at the specified visit. The registry’s Missing, Switch, or Discontinuation equals Failure algorithm treats participants without HIV-1 RNA data in the visit window as non-responders. It also treats certain switches in concomitant antiretroviral therapy as failures; the record says changes in antiretroviral therapy were not permitted by the protocol and participants who changed it were to be considered non-responders.

The comparison therefore concerns the proportion meeting the Week 48 viral-load threshold under that classification rule. It is not a comparison of average viral-load change, and the primary result alone does not describe every aspect of safety, tolerability, resistance, or longer-term outcomes.

3. Trial Design

The registry describes a Phase 3, randomized, quadruple-masked, parallel-group study of dolutegravir plus abacavir/lamivudine compared with Atripla. It enrolled 844 participants and is marked completed. The study population was adults with HIV-1 infection who had not previously received antiretroviral therapy. The registry lists ViiV Healthcare as the sponsor.

The planned treatment period in the official title was 96 weeks. The brief summary describes assessment of non-inferior antiviral activity over 48 weeks, with non-inferiority also to be tested at Week 96, and says that longer-term antiviral activity, tolerability, safety, and viral resistance would be evaluated. The posted primary endpoint is the proportion with HIV-1 RNA below 50 c/mL at Week 48. Secondary outcomes listed in the record extend to Week 144 and include viral suppression, viral-load and CD4+ cell-count changes, HIV-associated conditions, and clinical and hematology toxicities.

The arm descriptions specify once-daily treatment and placebo regimens to maintain masking. They describe approximately 394 participants in each arm, while the posted primary endpoint analyses report 414 and 419 participants in the respective groups. These figures belong to different descriptions in the record; the reason for the difference is not reported in the registry record. The primary endpoint population is defined as randomized participants who received at least one dose of study medication.

The study start date is 2011-02-01, and the primary completion date is 2012-05-14. The registry record does not report the planned non-inferiority margin, the rationale for the original sample size, or the full prespecified statistical analysis plan. Consequently, the observed results can be described, but the original design choices cannot be reconstructed from this record alone.

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: A total of 844 participants (par.) were randomized (1:1) to one of the two treatment arms. Of these, 833 par. received at least one dose of study medication. Of the 11 par. who were randomized but not treated with investigational product, 7 par. withdrew consent, 3 par. were randomized in error, and 1 par. was lost to follow-up.

Double-blind Phase: 96 Weeks Duration

Reasons for not completing this period:

Open-label Phase: 48 Weeks Duration

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat-Exposed (ITT-E) Population: all randomized participants who received at least one dose of study medication

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 Proportion of Subjects Responding Based on Plasma HIV-1 RNA <50 c/mL at Week 48, measured over Week 48.

The primary endpoint is the percentage of participants with plasma HIV-1 RNA below 50 c/mL at Week 48. This threshold defines a virologic response at a specified follow-up visit. Because the endpoint assigns each participant a response status, it can be summarized as a proportion in each treatment group and compared as a difference in proportions.

A threshold-based response is useful in a clinical trial because it gives a clear, interpretable classification of viral suppression at a planned time point. It is different from measuring the average change in viral load: two groups could have similar response proportions while differing in the distribution of viral-load changes among participants, or the reverse. The endpoint is also specific to the Week 48 assessment and does not by itself establish the response pattern at other visits.

The record defines the primary outcome using the Missing, Switch, or Discontinuation equals Failure algorithm, described as codified by the FDA Snapshot algorithm. Participants without an HIV-1 RNA assessment in the relevant visit window because of missing data or discontinuation of study product are counted as non-responders. Certain switches in concomitant antiretroviral therapy are also classified as failures. Since treatment changes were not permitted by the protocol, the record says that participants who changed antiretroviral therapy were to be considered non-responders. Otherwise, virologic success or failure was based on the last available on-treatment HIV-1 RNA assessment within the visit window.

This rule makes missingness and treatment changes part of the endpoint definition rather than simply excluding those participants from the response calculation. It does not remove every possible source of bias, but it makes the handling specified for this primary outcome explicit.

7. Results Posted in the Registry

• EFV/TDF/FTC 600/200/300 mg Once Daily: 80.9% (339/419) versus 87.9% (364/414) on control; risk difference -7.0 percentage points (95% CI -11.9 to -2.1), risk ratio 0.92 (0.87–0.98); unadjusted two-proportion z-test p = 0.005.

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.

Change From Baseline in CD4+ Cell Counts at Week 144

• 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:
  • EFV/TDF/FTC 600/200/300 mg Once Daily: mean 331.57 versus 378.48 on control; difference -46.91 (95% CI -48.44 to -45.38), standardized effect d = -4.15; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for EFV/TDF/FTC 600/200/300 mg Once Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the Symptom Bother Score (SBS) at Week 4 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 errors.
• Result:
  • EFV/TDF/FTC 600/200/300 mg Once Daily: mean -1.25 versus -1.82 on control; difference 0.57 (95% CI -0.50 to 1.64), standardized effect d = 0.07; z-test p = 0.294.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between EFV/TDF/FTC 600/200/300 mg Once Daily and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several distinct domains: viral suppression at later visits, time to suppression, viral-load change, CD4+ cell-count change, HIV-associated conditions, and clinical or hematology toxicities. They do not all measure the same construct as the Week 48 primary endpoint. The primary outcome is a binary viral-load response at one visit; secondary measures can describe trajectories, immune-cell counts, symptoms, or safety events.

The posted secondary results are not a complete, uniform set of estimates across all listed outcomes. The registry record includes a Week 144 CD4+ cell-count result analyzed with a repeated-measures mixed model and a symptom-bother score over Baseline and Week 4 through Week 48. The available secondary analyses therefore provide additional context but do not amount to a comprehensive confirmation of the primary result across every listed outcome and time point. Estimates, methods, or results for other secondary outcomes are not reported in the registry record.

Different patterns across secondary outcomes would not by themselves contradict the primary endpoint, because the outcomes differ in definition, measurement scale, follow-up schedule, and statistical method. Likewise, a secondary result in the same direction would not independently establish the primary question. Interpretation should take account of how many outcomes were considered, whether their analyses were prespecified, and whether adjustment or a testing hierarchy was used.

The registry does not report a multiplicity-control strategy for secondary analyses. When multiple outcomes and time points are examined, unadjusted p-values carry less confirmatory weight because they do not account for the full set of tests. Secondary findings are best considered supportive or hypothesis-generating unless a prespecified analysis plan establishes a stronger role. The primary endpoint remains the most direct answer to the stated Week 48 virologic question, while secondary outcomes broaden the description without resolving limitations in the primary analysis documentation.

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

• Time to Viral Suppression (<50 c/mL)
• Percentage of Participants With Plasma Human Immunodeficiency Virus -1 (HIV-1) Ribonucleic Acid (RNA) <50 Copies/Milliliter (c/mL) at Week 96 and Week 144
• Number of Participants With a Confirmed Plasma HIV-1 RNA Level >=1000 c/mL at or After Week 16 and Before Week 24, or a Confirmed Plasma HIV-1 RNA Level >=200 c/mL at or After Week 24
• Change From Baseline in Plasma HIV-1 RNA at Weeks 2, 4, 8, 12, 16, 24, 32, 40,48, 60, 72, 84, 96, 108, 120, 132 and 144
• Change From Baseline in CD4+ Cell Counts at Week 144
• Change From Baseline in CD4+ Cell Counts at Weeks 4, 8, 12, 16, 24, 32, 40, 48, 60, 72, 84, 96, 108, 120, 132 and 144
• Number of Participants With the Indicated Post-baseline HIV-associated Conditions and Progression, Excluding Recurrences at Week 144
• Number of Participants With the Indicated Grade 1 to 4 Clinical and Hematology Toxicities at Week144

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: participants are classified according to whether plasma HIV-1 RNA is below 50 c/mL at Week 48. A proportion summarizes the fraction classified as responders in a group. Comparing two such proportions can be expressed as a risk difference, which subtracts one group’s response proportion from the other’s. The sign depends on which group is subtracted from which, so the order of comparison must be kept in view when interpreting a positive or negative estimate.

The registry reports both a sponsor analysis and summary information from which an unadjusted comparison can be recalculated. The sponsor’s reported method is Wilcoxon (Mann-Whitney), with the parameter described as difference in percentage. Its reported result is an estimated difference of 7.3, a 95% confidence interval from 2.3 to 12.2, and p = 0.003. The recalculated comparison uses the posted response counts and denominators to form an unadjusted risk difference and its interval. It is a simple summary-statistic calculation, not a reconstruction of the sponsor’s full analysis. Because the two results are expressed in opposite group orders, their signs should not be compared without accounting for that orientation.

A confidence interval gives a range of values compatible with the data under the method and assumptions used. It communicates uncertainty about the estimated group difference; it does not mean that the true value has a specified probability of lying within that particular interval. A narrower interval indicates greater precision under the same framework. An interval that includes zero is compatible with no group difference under that framework, while one that excludes zero indicates that zero is not within the interval. Neither feature, on its own, answers a non-inferiority question: that requires comparison with the prespecified margin.

A p-value describes how unusual data at least as incompatible with a null hypothesis would be if that hypothesis and the method’s assumptions held. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. The unadjusted p-value from a recalculation should also be distinguished from the sponsor’s reported p-value, because the analyses need not use identical estimands or methods.

The missing-data rule is central to interpretation of the primary endpoint. Under the registry’s Missing, Switch, or Discontinuation equals Failure algorithm, a participant without an HIV-1 RNA assessment in the visit window because of missing data or study-product discontinuation is classified as a non-responder. Certain changes to concomitant antiretroviral therapy are also failures. In other cases, the last available on-treatment viral-load assessment in the visit window determines success or failure. This approach avoids treating missing primary outcome values as if they were observed successes, but the resulting response proportion depends on the classification rule. The record does not provide a sensitivity analysis comparing alternative missing-data assumptions.

The primary analysis population is Intent-to-Treat-Exposed: randomized participants who received at least one dose of study medication. This definition excludes randomized participants who did not receive study medication, if any; the record does not give a separate primary result for all randomized participants. The distinction matters because analysis populations answer different questions. The treated, randomized population describes outcomes among those who began study medication, while an all-randomized analysis would retain everyone assigned regardless of treatment initiation.

For the Week 144 CD4+ cell-count outcome, the registry reports least-squares means and a repeated-measures mixed-model analysis. A mixed model uses the repeated observations over time to estimate outcome patterns while accounting for the correlation of measurements from the same participant. Such models can use available repeated measurements, but their interpretation depends on model specification and assumptions about missing observations. The full model specification, covariates, and missing-data assumptions are not reported in the registry record. The posted recalculation from endpoint summaries is not the same as that model-based analysis and should not be treated as its substitute.

The symptom-bother outcome is reported as a least-squares mean change over Baseline and Week 4 through Week 48, with standard errors. A standard error describes the estimated uncertainty of a mean, whereas a standard deviation describes variation among observations. The posted recalculation for that outcome uses the summary values and is unadjusted; it does not recreate a model that may account for repeated observations or other design features. No sponsor-reported analysis is listed for that outcome in the registry record.

Multiplicity arises because several outcomes and time points are assessed. If many hypotheses are tested, the chance of at least one nominally unusual result can increase unless the analysis plan addresses that issue. The registry record lists 11 outcome measures and reports four analyses, but does not report a multiplicity adjustment strategy or a hierarchy for interpreting secondary outcomes. Therefore, unadjusted secondary p-values should be treated as exploratory or supportive rather than as a set of independently confirmatory findings.

The planning illustrations use observed effects as inputs under stated assumptions: a two-sided significance level of 0.05, equal allocation between groups, and a normal approximation. They scale the effect to be detected to the stated fraction of the observed effect. Such calculations show how assumed effect size relates to required sample size under those planning assumptions; they do not recover the trial’s original design. The original sample-size justification and design assumptions are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor’s Week 48 estimate is reported as a difference in percentage of 7.3, with a 95% confidence interval from 2.3 to 12.2. The interval is entirely above zero in the sponsor’s stated direction of comparison. Its width represents uncertainty around the estimated difference under the sponsor’s method; it is not a range of individual participant responses and does not show how responses vary within either group.

The unadjusted recalculation uses the opposite group order and reports a risk difference with a 95% confidence interval from -0.119 to -0.021. That interval is also entirely on one side of zero, but in a negative direction because the comparator group is subtracted from the other group in the opposite order. These estimates should be kept distinct: the sponsor’s reported analysis takes precedence over a simple recalculation, and the recalculation is not a replacement for the sponsor’s analysis.

Confidence intervals quantify uncertainty conditional on the selected analysis and its assumptions. They do not account automatically for every source of uncertainty, such as the choice of endpoint, missing-data rule, multiplicity across outcomes, or possible limitations in registry reporting. For a non-inferiority interpretation, the interval must be evaluated against a prespecified non-inferiority margin. That margin is not reported in the registry record, so the degree to which the interval satisfies the original criterion cannot be determined from the posted record alone.

The distinction between statistical precision and clinical importance also matters. A confidence interval can describe how precisely a group contrast is estimated, but it does not determine whether a difference is important to patients or whether it changes the balance of benefits and harms. The primary result addresses one viral-load threshold at Week 48, using the stated response and missing-data rules. It should not be read as a confidence interval for outcomes at other visits or for all aspects of treatment.

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 estimate the number of participants per arm for the binary and continuous outcomes shown. For time-to-event planning displays, the figure is the total number of events rather than participants per arm; the listed primary and secondary outcomes discussed in the planning displays are not time-to-event event-count calculations. The original trial’s sample-size assumptions are not reported in the registry record, so these illustrations should not be mistaken for the design calculation used to plan this study.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used is a stated fraction of the observed effect: the full observed effect, 75% of the observed effect, or 50% of the observed effect. The calculations are planning illustrations based on those assumptions, not estimates of the sample size required under every possible analysis or clinical setting.

The 80% power column gives the estimated participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under the calculation’s assumptions. The 90% power column gives the corresponding estimate for a 90% chance. Power is a design quantity defined for a particular assumed effect and statistical test; it is not a probability that the observed result is correct.

Smaller effects generally require more participants to detect, all else being equal. That relationship is reflected by the displays for progressively smaller fractions of the observed effect. An effect estimated from one completed trial may be unusually large or small, so planning directly from it can produce fragile projections. These figures are not observed power; they are hypothetical sample-size illustrations, and they should not be interpreted as evidence about the probability that the completed trial detected a true effect.

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 = 0.879; treatment proportion p₁ = 0.809; average p̄ = 0.844.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5130 = 1.0054.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5106 = 0.4297.
4. n = (1.0054 + 0.4297)² / (-0.0702)² = 418.4, rounded up to 419 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 <- 0.879227053140097                          # control proportion
p1 <- 0.809069212410501                          # 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(1263015)
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 = 419 (80% power), 560 (90% power)
 75% of observed effect: n per arm = 711 (80% power), 951 (90% power)
 50% of observed effect: n per arm = 1,520 (80% power), 2,034 (90% power)
power.prop.test: 418.4 
Simulated power at n = 419 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 sponsor’s own reported primary analysis is the main result for interpreting the trial. It uses a Wilcoxon (Mann-Whitney) method and reports a difference in percentage of 7.3, a 95% confidence interval from 2.3 to 12.2, and p = 0.003. The registry classifies this reported analysis as non-inferiority or equivalence. The non-inferiority margin and the detailed decision rule are not reported in the registry record, so the label and numerical result can be described but the formal criterion cannot be checked independently.

The recalculated comparison is a simple, unadjusted calculation from posted group summaries. It gives a risk difference in the opposite direction of subtraction and a different unadjusted p-value. Different labels or signs in the two analyses do not necessarily signal contradictory group patterns: the subtraction order differs, and the recalculation does not reproduce the sponsor’s method. Because the registry record does not identify a discrepancy, the sponsor’s analysis takes precedence over the recalculation.

The recalculation can still help readers understand the posted group proportions and the scale and direction of a simple contrast. It should not be used to override the sponsor’s analysis or to infer the original non-inferiority conclusion without the missing margin. A p-value and interval are meaningful only in relation to their method, endpoint definition, analysis population, and comparison direction.

15. Multiplicity, Missing Data and Analysis Populations

The registry describes one primary Week 48 virologic response endpoint and lists a range of secondary outcomes, including measurements at multiple follow-up times. Testing several outcomes or time points raises a multiplicity issue: the more hypotheses examined, the greater the opportunity for at least one result to appear statistically unusual by chance when each test is viewed separately. This does not make secondary analyses uninformative, but it affects how strongly nominal p-values support a confirmatory claim.

The registry record does not report whether the secondary analyses were adjusted for multiplicity, whether a hierarchy of outcomes was prespecified, or how any family of tests was defined. It also does not report the full statistical analysis plan. As a result, unadjusted secondary p-values should be read as individual comparisons rather than as evidence that a trial-wide error rate was controlled.

Missing data are addressed explicitly for the primary endpoint through the Missing, Switch, or Discontinuation equals Failure algorithm. Missing HIV-1 RNA data in the visit window due to missingness or study-product discontinuation are classified as non-response, and certain changes in concomitant antiretroviral therapy are also treated as failures. Otherwise, the last available on-treatment viral-load result in the visit window determines response status. This is a defined analysis rule, not an observation of the unmeasured viral-load values.

The record does not report sensitivity analyses using alternative missing-data assumptions for the primary endpoint. Nor does it provide enough information to establish that the same rule or a comparable strategy was used for every secondary endpoint. For the repeated-measures CD4+ analysis, the model specification and assumptions about missing observations are not reported in the registry record. Those gaps limit assessment of how robust the secondary findings are to incomplete follow-up.

The primary analysis population is Intent-to-Treat-Exposed, defined as randomized participants who received at least one dose of study medication. A separate primary analysis of all randomized participants is not reported in the registry record. The distinction is relevant because excluding randomized participants who never began study medication can change the population to which the result directly applies. The registry gives no separate result allowing that comparison.

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: appendicitis (1.0%), suicide attempt (0.7%), bronchitis (0.7%), subcutaneous abscess (0.7%), depression (0.7%).

The registry reports serious adverse events for the two treatment groups as counts of affected participants and the corresponding number at risk. The posted figures are 65 of 414 for dolutegravir plus abacavir/lamivudine and 60 of 419 for Atripla. Other adverse events are reported for 332 of 414 and 358 of 419, respectively. These are descriptive counts, not adjusted comparisons, and they do not establish that a treatment caused an event or that the groups differ meaningfully in safety.

The listed serious-event terms include appendicitis at 1.0%, and suicide attempt, bronchitis, subcutaneous abscess, depression, and syncope at 0.7% each. These terms are examples from the registry’s listed serious-event terms and should not be interpreted as a complete account of all possible harms. The record does not report death counts in the posted safety summary.

Safety figures depend on how events were collected, coded, and summarized, as well as on follow-up and the number of participants assessed. The registry provides counts, but does not report a detailed comparative safety model or enough information in this summary to assess event timing, duration, severity distributions, or exposure-adjusted rates. These data therefore describe the posted adverse-event burden without supporting a broader causal or comparative safety conclusion.

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

The primary result describes the proportion of participants in each treatment group who met the Week 48 HIV-1 RNA threshold under the registry’s specified response rule. The sponsor reports a difference in percentage with a confidence interval and p-value, and the posted group percentages are higher in the dolutegravir plus abacavir/lamivudine group. That is a description of the observed trial result, not a general prediction for every person with HIV-1 infection or every treatment setting.

The study was described as testing non-inferiority, but the registry record does not report the margin used to define non-inferiority. Without that margin, the formal claim cannot be independently verified from the posted record. A statistically nonzero difference is not equivalent to satisfying a non-inferiority criterion, and a p-value is not a measure of clinical importance.

The endpoint is limited to a viral-load threshold at Week 48 and uses a failure classification for specified missing or changed-treatment cases. It does not on its own describe longer-term viral suppression, resistance, quality of life, all adverse effects, or the balance of outcomes important to an individual. The registry lists later outcomes, but does not report results for all listed measures in the available record.

The secondary analyses address additional outcomes and time frames, but they differ in methods and completeness. Their role is to add context, not to convert the primary result into a conclusion about every outcome. The absence of a reported multiplicity strategy further limits the confirmatory interpretation of unadjusted secondary findings.

Accordingly, the results support a narrowly framed statistical reading: the posted Week 48 response percentages and sponsor analysis describe a group comparison among the defined Intent-to-Treat-Exposed population, under the stated endpoint algorithm. They do not by themselves prove a treatment effect in every relevant sense, establish safety superiority, or provide individual medical guidance.

18. Why This Trial Matters Statistically

This trial illustrates why the estimand and analysis rule matter as much as the headline response percentages. A binary viral-load endpoint is easy to state, but its meaning depends on how missing assessments, discontinuation, and treatment changes are classified. The registry makes the primary classification rule explicit, allowing readers to understand that some participants without an in-window measurement are counted as non-responders rather than simply omitted.

It also demonstrates the importance of keeping a sponsor-reported analysis separate from a simple recalculation. The sponsor reports a Wilcoxon (Mann-Whitney) analysis for a non-inferiority or equivalence comparison, while the recalculated result is an unadjusted contrast derived from summary data. The two are not interchangeable. A recalculation can help with orientation and interpretation, but it cannot recover unreported model details or replace the sponsor’s method.

Non-inferiority questions require a prespecified margin. Even when a reported confidence interval is informative about the observed contrast, the margin is needed to assess whether the result meets the trial’s stated criterion. Its absence from the registry record is therefore an important interpretive limitation, not a minor reporting detail.

Finally, a wide portfolio of secondary outcomes makes multiplicity and analysis transparency important. Results for viral, immunologic, symptom, and safety measures can provide complementary perspectives, but each answers a different question. Explicit reporting of analysis populations, missing-data assumptions, model specifications, and multiplicity plans helps readers distinguish confirmatory evidence from supportive context.

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 or the complete original statistical analysis plan. Although the sponsor’s primary analysis is labelled as non-inferiority or equivalence, the decision threshold needed to verify that interpretation is unavailable in the record. The original sample-size justification and design assumptions are also not reported, so the planning illustrations cannot be treated as a reconstruction of the trial’s design.

The primary response rule is described, but sensitivity analyses under alternative missing-data assumptions are not reported. Since the endpoint classifies specified missing and changed-treatment cases as failures, the result depends in part on that rule. A separate primary result for all randomized participants is not reported; the stated primary population includes randomized participants who received at least one dose of study medication.

The registry lists multiple secondary outcomes, but the secondary reporting available in the record is incomplete. The multiplicity strategy, any outcome hierarchy, and full methods for the repeated-measures analyses are not reported. The model details and assumptions for the CD4+ analysis, including its handling of missing observations, are not available. The symptom-bother result has no sponsor-reported analysis listed in the record.

Safety reporting is also limited in the posted summary. Counts of participants with serious and other adverse events are available, along with selected serious-event terms, but the record does not provide a detailed comparative safety analysis in this summary. Death counts are not reported in the registry record. Event timing, duration, and exposure-adjusted comparisons are not available in the stated details.

These are limits of what the registry record reports, not proof that the study did not conduct additional analyses. They constrain independent assessment of the non-inferiority decision, robustness to missing data, multiplicity, secondary outcomes, and comparative safety.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Trial Comparing GSK1349572 50mg Plus Abacavir/Lamivudine Once Daily to Atripla (Also Called The SINGLE Trial) — NCT01263015.
• Registry record last updated 2018-04-04; status last verified 2018-03.
• Results first posted 2014-07-02.
• 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

The registry record describes a completed randomized, quadruple-masked, parallel-group Phase 3 trial in antiretroviral-therapy-naïve adults with HIV-1 infection. It compared once-daily dolutegravir plus abacavir/lamivudine with once-daily Atripla. The primary endpoint was the proportion with plasma HIV-1 RNA below 50 c/mL at Week 48 in the Intent-to-Treat-Exposed population, using a Missing, Switch, or Discontinuation equals Failure response rule.

The sponsor reported a difference in percentage of 7.3, with a 95% confidence interval from 2.3 to 12.2 and p = 0.003, in an analysis labelled non-inferiority or equivalence. The non-inferiority margin is not reported in the registry record. A simple recalculation from posted summaries is available as a separate, unadjusted comparison and does not replace the sponsor’s analysis.

The registry lists a broad set of secondary and safety outcomes, but methods and results are not reported for all of them. The multiplicity plan, full analysis plan, and original sample-size justification are not reported in the registry record.