Standard Versus Double Dose Dolutegravir in Patients With HIV-associated Tuberculosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Standard Versus Double Dose Dolutegravir in Patients With HIV-associated Tuberculosis (NCT03851588), a randomized phase 2 study. The primary outcome is Virological Suppression at 24 Weeks.

2. Clinical Question

The registry record describes a phase 2 randomized comparison of supplementary dolutegravir against placebo in the setting of rifampicin-based tuberculosis treatment. The central statistical question is whether the observed proportion meeting the viral-suppression definition differed between the groups at the specified follow-up time. The endpoint is binary: each participant either meets the suppression criterion at 24 weeks under the stated algorithm or does not.

The record reports 43.0 participants meeting the endpoint among 52.0 in the supplementary-dose group and 44.0 among 53.0 in the placebo-dose group. The unadjusted risk difference, expressed as supplementary dose minus placebo dose, is -0.003. Its confidence interval extends from -0.147 to 0.141, so the posted summary counts are compatible with differences in either direction. The comparison is descriptive and should not be read as establishing equivalence or as proving that a difference is absent.

The trial’s stated hypothesis concerned acceptable virologic outcomes with standard-dose dolutegravir-based therapy during rifampicin-based tuberculosis treatment. The primary outcome comparison also provides information about the supplementary-dose strategy, but a non-comparative phase 2 trial designation does not by itself establish a formal equivalence or non-inferiority question. The registry record does not report a non-inferiority margin or an equivalence criterion.

3. Trial Design

The registry record identifies a phase 2, randomized, parallel-group trial with triple masking. Its official title describes it as a non-comparative randomized controlled trial, while the brief summary describes a randomized, double-blind, placebo-controlled design. Participants received the same daily dolutegravir-lamivudine-tenofovir fixed-dose combination in both groups; the randomized difference was an additional dolutegravir 50 mg dose taken 12 hours later or a matching placebo taken at that time.

The enrolled population was described as ART-naïve or first-line interrupted people with HIV infection who were receiving rifampicin-based anti-tuberculosis therapy. The listed conditions are HIV infections and tuberculosis. The record identifies the University of Cape Town as sponsor. It lists the trial status as completed, with an enrollment of 108, a start date of 2019-12-19 and primary completion on 2022-01-20.

The primary outcome was virological suppression at 24 weeks, measured as the count of participants whose HIV viral load was <50 copies/mL. The analysis population was modified intention to treat and included participants who received at least one dose of dolutegravir. The outcome description specifies use of the FDA snapshot algorithm. These definitions matter: the reported endpoint is not simply a laboratory measurement detached from the stated population and analysis rule, but a classified outcome at a particular follow-up time.

Other registry outcomes include virological suppression at 12 and 48 weeks, a per-protocol assessment at 24 weeks, CD4 change, dolutegravir trough concentrations, grade 3 or 4 adverse events, and sleep assessment. The registry record lists 14 outcome measures and 13 posted secondary outcomes. It does not report the trial’s original sample-size justification, detailed randomization procedures, or a full statistical analysis plan. The record also does not report whether interim analyses were planned or conducted.

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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: mITT population at 24 weeks

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 Virological Suppression at 24 Weeks, measured over 24 weeks.

The primary endpoint counts participants with an HIV viral load <50 copies/mL at 24 weeks. It is analyzed in the modified intention-to-treat population, which the registry record defines as participants who received at least one dose of dolutegravir. Classification follows the FDA snapshot algorithm. The endpoint is therefore a binary outcome: the count meeting the stated suppression criterion is considered in relation to the number in the analysis group.

A viral-load threshold gives the trial a specific, interpretable way to classify virological status at the selected follow-up time. For statistical comparison, a binary outcome allows the groups to be described by their observed suppression proportions and compared using a risk difference. That difference expresses how far apart the proportions are on the absolute probability scale, with the sign depending on which group is subtracted from which. Here the comparison is supplementary dose minus placebo dose.

The endpoint is useful for describing the trial’s virological result, but it captures status at the specified assessment rather than the entire course of viral load over time. The FDA snapshot rule and modified intention-to-treat population also shape how participants are counted. Interpretation should therefore remain tied to the stated definition, follow-up point, and analysis population. The registry record does not provide additional detail on the handling of specific missing or unevaluable endpoint measurements beyond naming the snapshot algorithm.

7. Results Posted in the Registry

• Supplementary Dose: 82.7% (43/52) versus 83.0% (44/53) on control; risk difference -0.3 percentage points (95% CI -14.7 to 14.1), risk ratio 1.00 (0.84–1.19); unadjusted two-proportion z-test p = 0.965.

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.

Virological Suppression at 12 Weeks (Modified ITT)

• 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:
  • Supplementary Dose: 79.2% (42/53) versus 83.6% (46/55) on control; risk difference -4.4 percentage points (95% CI -19.0 to 10.3), risk ratio 0.95 (0.79–1.14); unadjusted two-proportion z-test p = 0.557.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Supplementary Dose and the control. The interval gives the range of effects that remain compatible with the data.

Virological Suppression at 24 Weeks (Per Protocol)

• 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:
  • Supplementary Dose: 84.3% (43/51) versus 84.6% (44/52) on control; risk difference -0.3 percentage points (95% CI -14.3 to 13.7), risk ratio 1.00 (0.84–1.18); unadjusted two-proportion z-test p = 0.966.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Supplementary Dose and the control. The interval gives the range of effects that remain compatible with the data.

Virological Suppression at 48 Weeks (Modified ITT)

• 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:
  • Supplemental Dolutegravir Arm: 69.4% (34/49) versus 67.3% (35/52) on control; risk difference 2.1 percentage points (95% CI -16.1 to 20.2), risk ratio 1.03 (0.79–1.34); unadjusted two-proportion z-test p = 0.822.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Supplemental Dolutegravir Arm and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary virological outcomes provide additional observations at different follow-up times and under different analysis populations. Their overall pattern is broadly consistent with similar observed proportions between groups at the earlier assessments, while the 48-week modified intention-to-treat proportions are lower in both groups. A per-protocol assessment at 24 weeks is also listed. These results add context to the primary endpoint but do not replace it: follow-up time and analysis population affect what each estimate describes.

The secondary outcomes extend beyond viral suppression to include CD4 change, dolutegravir trough concentrations, grade 3 or 4 adverse events, and sleep assessment. They address different dimensions and are not all measures of the same treatment effect. Their relevance depends on their definitions, populations, measurement schedules, and analysis methods. The registry record lists 13 posted secondary outcomes, but does not report formal analyses for them.

Unadjusted secondary comparisons generally carry less evidential weight than a prespecified primary analysis. When many outcomes or time points are examined, some apparent differences can occur by chance even when no corresponding underlying difference exists. Multiplicity methods can address that issue, but a correction strategy or hierarchy for interpreting secondary outcomes is not reported in the registry record. The secondary findings should therefore be treated as descriptive or exploratory rather than as independent confirmatory evidence.

The secondary results can help identify patterns that may warrant further study, but they should be interpreted alongside the primary estimate and its uncertainty. They do not provide a basis for strengthening the primary result into a claim of equivalence, nor do differing estimates at separate time points necessarily imply a real change over time. The record does not report a formal longitudinal analysis comparing changes across visits.

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

• Virological Suppression at 12 Weeks (Modified ITT)
• Virological Suppression at 24 Weeks (Per Protocol)
• Virological Suppression at 48 Weeks (Modified ITT)
• Virological Suppression at 48 Weeks (Per Protocol)
• CD4 Change at 24 Weeks
• Dolutegravir Trough Concentrations
• Grade 3 or 4 Adverse Events
• Change in Sleep Assessment From Baseline - Any Treatment Emergent Insomnia After Baseline Assessed at 4 Weekly Intervals Until Week 24 and Then Again at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference represent?

A risk difference compares the proportions with an event in two groups by subtracting one proportion from the other. In this trial, the stated direction is supplementary dose minus placebo dose. A negative estimate means the observed proportion meeting the endpoint was lower in the supplementary-dose group; a positive estimate would mean it was higher. The estimated risk difference is -0.003. Because the endpoint is binary, this measure directly describes an absolute difference in the probability of meeting the viral-suppression definition, rather than a relative change.

The group proportions are 0.827 for supplementary dose and 0.830 for placebo dose. The comparison uses the observed counts and group sizes, without adjustment for other variables. The registry record does not report an adjusted primary analysis. An unadjusted estimate is straightforward to interpret, but it does not account for possible imbalances in participant characteristics or other covariates. Randomization is intended to support a fair group comparison, though a modest trial can still have chance imbalances.

How should the confidence interval be read?

A confidence interval describes the range of effect estimates reasonably compatible with the observed data under the calculation’s assumptions. It is not a range containing a fixed proportion of individual participant outcomes, and it does not assign a probability to each specific effect value. For the primary risk difference, the interval is -0.147 to 0.141. It includes no difference and also includes differences favoring either group. Its width signals that the estimate is not highly precise.

For a binary outcome, the observed group proportions are estimates of underlying probabilities. The confidence interval reflects sampling uncertainty in the difference between those estimates. In general, more information can narrow an interval, while sparse data or substantial variability can leave an interval wide. Those are general statistical principles; the interval itself should be interpreted in the context of this trial’s population, endpoint definition, and analysis approach.

What does the p-value say?

The unadjusted p-value is 0.965. In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, nor is it a measure of the clinical importance of an effect. The large value does not prove that the groups are identical. The confidence interval is more informative about the range of differences compatible with the data.

The comparison is described as unadjusted and is based on posted summary statistics. It should not be confused with an analysis adjusted for baseline variables, stratification factors, or repeated measurements. The registry record lists no reported analyses, and does not give a detailed inferential-analysis plan. Consequently, the exact analysis procedures specified by investigators beyond the endpoint definition are not reported in the registry record.

Why do the analysis population and snapshot rule matter?

The primary endpoint uses a modified intention-to-treat population, defined in the record as including all participants who received at least one dose of dolutegravir. This is not the same as an analysis that necessarily includes every randomized participant regardless of treatment received. The endpoint description further specifies the FDA snapshot algorithm. Such an algorithm defines how outcome status is assigned at a given visit, including how the analysis handles the endpoint classification under the algorithm’s rules. The record does not provide additional detail about the treatment of each missing or unevaluable measurement, so that detail is not reported in the registry record.

The per-protocol secondary outcome at 24 weeks uses a different analysis population from the primary modified intention-to-treat endpoint. Different populations can produce different estimates because the participants included in the calculation differ. They also answer somewhat different questions: the modified intention-to-treat result follows the record’s treated-participant definition, while a per-protocol result reflects the subset meeting the protocol-based analysis definition. The registry record does not specify the full criteria for per-protocol inclusion.

What does generalizability mean in this setting?

Generalizability concerns whether results from the enrolled trial population apply to people or settings beyond those represented. As a general statistical concept, it depends on how closely the trial population, treatment context, and outcome assessment match the intended setting of interest. The record describes people with HIV-associated tuberculosis receiving rifampicin-based therapy and compares two supplementary-dose strategies on a common background regimen. It does not establish that the same estimates apply to populations or treatment circumstances outside that description.

The trial’s phase 2 and non-comparative design labels are relevant context, but they do not substitute for a stated margin or a prespecified analysis plan. A near-zero estimate in a finite sample may coexist with substantial uncertainty. The statistical conclusion should therefore be limited to the observed endpoint comparison and its confidence interval rather than extended to a stronger claim of equivalence, non-inferiority, or absence of any effect.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.003, and its confidence interval extends from -0.147 to 0.141. This interval is broad relative to the point estimate and crosses zero. It is compatible with a small difference in either direction as well as larger differences in either direction. The point estimate alone may look close to zero, but the interval shows that the posted results do not precisely pin down the underlying difference.

In general, a confidence interval summarizes sampling uncertainty around an estimate. It should not be read as a guarantee that the true value lies inside it, or as a probability statement about a particular value. Its practical meaning depends on the outcome scale and the range of effects that would matter for the research question. The registry record does not report a threshold defining what size of difference would be considered acceptable, so the interval cannot be judged against a stated non-inferiority or equivalence margin.

The unadjusted p-value of 0.965 is consistent with the interval including zero, but neither statistic establishes that the groups are identical. The trial’s enrollment and observed endpoint counts provide limited information for estimating a difference precisely. The confidence interval is thus central to interpretation: it conveys that the result is inconclusive about the direction and size of the underlying risk difference, despite similar observed proportions.

Precision is distinct from whether an estimate is biased or clinically important. The interval addresses uncertainty under the calculation’s assumptions; it does not resolve limitations in endpoint definition, missing-data handling, or generalizability. The registry record does not report the detailed analysis plan needed to assess every such issue. The appropriately cautious reading is that the observed groups had similar proportions on this endpoint, while the plausible range remains wide.

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 participants per arm for the binary outcomes in this trial; they are not total event counts. The listed illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as its reference and considers planning for 100%, 75%, or 50% of that observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm under those assumptions for a design with 80% power to detect the stated effect. The 90% power column gives the corresponding number per arm for a design with 90% power. In general, higher target power requires more participants under otherwise comparable assumptions. Planning for a smaller effect also requires more participants, because smaller group differences are harder to distinguish from sampling variation.

These figures are planning illustrations based on the observed effect, not evidence that the trial had a particular probability of detecting an effect after the results were known. They are not observed power. The observed effect in a small trial can be unstable, so using it as a planning basis is illustrative rather than a substitute for a design justification based on a prespecified effect of interest. The record does not report the investigators’ original target effect, target power, or sample-size calculation, and those details cannot be inferred from these planning figures.

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 = 0.830; treatment proportion p₁ = 0.827; average p̄ = 0.829.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5330 = 1.0447.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5330 = 0.4486.
4. n = (1.0447 + 0.4486)² / (-0.0033)² = 209,099.5, rounded up to 209,100 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 <- 0.830188679245283                          # control proportion
p1 <- 0.826923076923077                          # 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(3851588)
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 = 209,100 (80% power), 279,925 (90% power)
 75% of observed effect: n per arm = 371,032 (80% power), 496,705 (90% power)
 50% of observed effect: n per arm = 833,239 (80% power), 1,115,471 (90% power)
power.prop.test: 209099.5 
Simulated power at n = 209,100 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple outcomes, including virological suppression at several follow-up times, different analysis populations, immunologic and pharmacokinetic measures, adverse events, and sleep assessment. Examining multiple outcomes creates a multiplicity concern: the chance of encountering at least one apparently notable result can increase as more comparisons are considered. This is a general statistical issue, not evidence that any particular result is false.

A prespecified hierarchy, adjustment procedure, or distinction between confirmatory and exploratory analyses can help define how multiple results should be interpreted. Such a strategy is not reported in the registry record. The record also lists zero reported analyses, so there is no posted analysis narrative describing how multiplicity was handled. Consequently, the unadjusted secondary comparisons should not be treated as though they were protected by a stated family-wise error or false-discovery procedure.

The primary endpoint is described with a modified intention-to-treat population and the FDA snapshot algorithm. The record defines the modified intention-to-treat population as participants who received at least one dose of dolutegravir, but does not give detailed rules for missing viral-load measurements, discontinuations, or other specific endpoint situations. The exact handling of those cases beyond the named snapshot algorithm is not reported in the registry record. This limits independent assessment of how missingness may have affected the observed proportions.

A per-protocol 24-week secondary result is also posted, but the record does not describe the full criteria defining that population. Per-protocol analyses can be informative, yet they may be affected by post-randomization exclusions and can differ in interpretation from a randomized-group analysis. The registry record does not report a detailed comparison of missingness or adherence between groups.

The record does not report an interim-analysis plan, stopping rules, or a detailed statistical analysis plan. Their absence from the registry record should not be taken as proof that none existed; the relevant point is that they cannot be evaluated from the reported information. Overall, multiplicity handling, detailed missing-data procedures, and several analysis-population definitions remain unreported, so secondary and subgroup-style interpretations require caution.

15. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: treatment resistant oesophageal candidiasis (1.8%), lichenoid rash secondary to tb treatment (1.8%), bowel obstruction (1.8%), trauma (1.8%), community acquired pneumonia (1.8%).

The safety record reports serious adverse events among 53 participants at risk in the supplementary-dose group and 55 at risk in the placebo-dose group. It records 0 serious adverse events in the supplementary-dose group and 5 in the placebo-dose group. Deaths are listed as 0 and 3, respectively. These are the posted counts; they should be read as descriptive safety information rather than as a definitive comparison of risk.

The registry also lists 3 other adverse events in the supplementary-dose group and 0 in the placebo-dose group, with the same group-specific numbers at risk as for the safety summary. The record lists five top serious-event terms, each at 1.8%: treatment resistant oesophageal candidiasis, lichenoid rash secondary to TB treatment, bowel obstruction, trauma, and community acquired pneumonia. The listed terms do not establish that each event was caused by a study treatment.

Safety counts are not the same as a complete causal assessment. The registry record does not report a formal comparative safety analysis, confidence intervals for these counts, or further detail about event timing and attribution. Group denominators for the safety summaries also differ from the primary endpoint analysis groups. These findings describe what was posted and do not establish that one regimen is safer.

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

The primary result describes virological suppression at 24 weeks under a specific definition: HIV viral load <50 copies/mL, assessed in the modified intention-to-treat population using the FDA snapshot algorithm. The observed proportions were 0.827 with supplementary dolutegravir and 0.830 with placebo. The unadjusted risk difference was -0.003, with a confidence interval from -0.147 to 0.141 and an unadjusted p-value of 0.965.

These data do not show a clear difference between the groups in the posted primary comparison. They also do not demonstrate that the strategies are identical. The interval includes zero and allows for differences in both directions; the point estimate’s closeness to zero does not remove that uncertainty. The registry record does not report a prespecified equivalence or non-inferiority margin, so the result cannot establish either form of conclusion.

The result applies directly to the described trial context: ART-naïve or first-line interrupted people with HIV-associated tuberculosis receiving rifampicin-based anti-tuberculosis therapy and the stated background regimen. It is not a universal estimate for all people with HIV or tuberculosis, all treatment settings, or other outcome definitions. The registry record does not report enough detail to determine how specific missing or unevaluable viral-load assessments were handled beyond the named snapshot algorithm.

The secondary outcomes and safety counts offer additional descriptive information, but the record does not report a multiplicity strategy or formal analyses for them. They should not be used to make stronger claims than the primary result supports. In particular, neither the primary estimate nor the secondary pattern proves that there is no treatment difference or that either strategy is preferable. The sound statistical conclusion is limited: the observed primary proportions were similar, while the interval leaves substantial uncertainty about the size and direction of the underlying difference.

17. Why This Trial Matters Statistically

This trial illustrates why interpreting a clinical comparison requires more than looking at whether the observed group proportions are close. The primary endpoint proportions are similar, and the estimated risk difference is close to zero, but the confidence interval is wide and includes meaningful differences in either direction. Statistical precision is therefore central to the interpretation.

The record also illustrates the distinction between a randomized comparison and an equivalence or non-inferiority study. A randomized trial can estimate a difference between groups, but a conclusion that strategies are sufficiently similar requires a prespecified margin and an analysis designed to assess that margin. The registry record does not report such a margin. A non-significant or near-zero comparison is not, by itself, proof of equivalence.

Outcome definitions and analysis populations also matter. The primary result uses a modified intention-to-treat definition and the FDA snapshot algorithm, while the secondary outcomes include different time points and a per-protocol assessment. Those choices shape what is estimated and make it important not to treat every outcome as interchangeable.

Finally, the many listed outcomes raise the need for transparent multiplicity and analysis-plan reporting. The registry record does not report a multiplicity strategy or detailed analysis plan. This limits how strongly secondary findings can be interpreted. The trial is statistically informative as an example of a modest phase 2 comparison with descriptive outcome counts and substantial uncertainty, while also showing why design assumptions, analysis rules, and precision should be reported clearly.

18. 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.

The primary comparison is based on the posted group counts and an unadjusted estimate. No adjusted primary analysis is reported. The confidence interval is wide, so the estimate does not narrowly determine the direction or size of a group difference. The registry record does not report the original sample-size justification, making it difficult to assess whether the trial was designed for a particular effect size or precision target.

The official title calls the trial non-comparative, while the design fields identify randomized parallel groups and the brief summary describes a placebo-controlled comparison. This makes it especially important not to assume an equivalence or non-inferiority framework: neither a margin nor such a formal objective is reported. The endpoint comparison can describe observed differences, but does not establish that the strategies are interchangeable.

The primary outcome is limited to a particular threshold at 24 weeks and a modified intention-to-treat population defined by receipt of at least one dose. The registry record names the FDA snapshot algorithm but does not provide detailed case-level rules for missing, unevaluable, or discontinued participants. The full per-protocol criteria are also not reported. These omissions limit assessment of how analysis choices influence the estimates.

Multiple secondary outcomes and follow-up times are listed, but no multiplicity strategy or formal secondary analyses are reported. The safety information is also descriptive; the registry record does not report adjusted comparisons, confidence intervals, or detailed event attribution. Finally, the results pertain to the described population receiving rifampicin-based therapy and should not be assumed to apply to settings or populations outside that trial context.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Standard Versus Double Dose Dolutegravir in Patients With HIV-associated Tuberculosis — NCT03851588.
• Registry record last updated 2024-07-18; status last verified 2024-06.
• Results first posted 2023-09-18.
• 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.

22. Record Summary

The registry record describes a completed phase 2 randomized, triple-masked, parallel-group trial comparing supplementary dolutegravir with a matching placebo alongside daily dolutegravir-lamivudine-tenofovir in people with HIV-associated tuberculosis receiving rifampicin-based therapy. The primary endpoint was virological suppression at 24 weeks, defined as viral load <50 copies/mL in a modified intention-to-treat population under the FDA snapshot algorithm.

The posted primary proportions were 0.827 for supplementary dose and 0.830 for placebo dose. The unadjusted risk difference was -0.003, with a confidence interval from -0.147 to 0.141 and an unadjusted p-value of 0.965. The estimate is close to zero, but the interval is broad and does not establish equivalence or absence of a difference.

The record lists secondary virological, immunologic, pharmacokinetic, adverse-event, and sleep outcomes. It does not report the original sample-size justification, a detailed statistical analysis plan, multiplicity handling, or full missing-data procedures.