Safety and Efficacy of Bictegravir/Emtricitabine/Tenofovir Alafenamide Versus Dolutegravir + Emtricitabine/Tenofovir Disoproxil Fumarate in Treatment Naive, HIV-1 and Hepatitis B Co-Infected Adults: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Bictegravir/Emtricitabine/Tenofovir Alafenamide Versus Dolutegravir + Emtricitabine/Tenofovir Disoproxil Fumarate in Treatment Naive, HIV-1 and Hepatitis B Co-Infected Adults (NCT03547908), a randomized phase 3 study. The primary outcome is Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 48 as Defined by the US FDA-Defined Snapshot Algorithm (Co-primary Endpoint).

2. Clinical Question

The trial addressed virologic response in a population with both HIV-1 and hepatitis B infection, rather than in an HIV-1-only population. That distinction matters when interpreting the target population: the registry record describes treatment-naïve adults with both infections, so the posted response estimates concern that study population.

The randomized comparison was between two treatment strategies, not between active treatment and no treatment. The main contrast therefore concerns the relative Week 48 response percentages for B/F/TAF and DTG + F/TDF. The snapshot outcome classifies response at a specified visit window and takes treatment discontinuation status into account. It is not simply a measure of whether viral load ever fell below the threshold during follow-up.

The primary question is about both the observed response and the uncertainty in the between-group contrast. A difference in observed percentages does not by itself establish superiority or non-inferiority. Those conclusions depend on the prespecified comparison framework and, for non-inferiority, the margin. The margin and a full description of the planned statistical framework are not reported in the registry record.

3. Trial Design

This was a Phase 3, randomized, double-blind, parallel-group study. The registry lists enrollment of 244 participants and identifies HIV-1/HBV co-infection as the condition. The study status is completed. Its listed start date is 2018-05-30 and its primary completion date is 2022-02-25.

In the blinded phase, participants were assigned to B/F/TAF or DTG + F/TDF. Matching placebos were used: the B/F/TAF group received placebos matching DTG and F/TDF, and the DTG + F/TDF group received a placebo matching B/F/TAF. This arrangement is consistent with maintaining blinding across regimens with different tablet components. The registry identifies the study as double-blind but does not report further details about who was masked or how masking was assessed.

The arm descriptions state that the DTG + F/TDF group received its regimen with matching B/F/TAF placebo for 96 weeks. They also describe an open-label extension after Week 96. Participants were to continue blinded study drug and attend visits every 12 weeks until the End of Blinded Treatment Visit. The descriptions then mention an option to receive B/F/TAF in a country where the fixed-dose combination was not available. Further details of extension eligibility, duration, treatment changes, and analysis are not reported in the registry record.

The primary outcome was assessed at Week 48. The posted secondary outcomes include viral response at Week 96, CD4 cell-count changes at Week 48 and Week 96, and other immune, hepatitis B, and liver-enzyme measures. The registry lists 12 outcome measures and 14 analyses, with 10 secondary outcomes posted. The full protocol, the original sample-size justification, allocation concealment procedures, and details of any interim analyses are not reported in the registry record.

Enrollment of 244 describes the overall planned or registered enrollment figure; the primary endpoint analysis used 119 participants in the B/F/TAF group and 122 in the DTG + F/TDF group. The outcome-specific denominators can differ from those arm counts, as illustrated by the continuous secondary outcomes. The registry’s Full Analysis Set definition requires randomization, at least 1 dose, and at least 1 qualifying postbaseline result while on study drug.

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: 381 participants were screened.

Blinded Phase

Reasons for not completing this period:

Open-label Extension Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set included all participants who were randomized into the study, received at least 1 dose of study drug, and had at least 1 postbaseline HIV-1 RNA or HBV DNA result while on study drug.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: The Safely Analysis Set included participants who were randomized into the study and received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 48 as Defined by the US FDA-Defined Snapshot Algorithm (Co-primary Endpoint), measured over Week 48.

The primary endpoint is the percentage of participants with HIV-1 RNA < 50 copies/mL at Week 48, defined using the US FDA-defined Snapshot algorithm. The endpoint is a binary virologic-response measure summarized as a percentage: each participant is classified according to whether the threshold is met under the algorithm’s rules.

As described in the registry, the Snapshot algorithm uses the viral-load result at a predefined time point within an allowed visit window together with study-drug discontinuation status. Thus, the result reflects response at the scheduled assessment and is not an unrestricted count of everyone who may have reached the threshold at any time. Incorporating discontinuation status also means that treatment discontinuation can affect response classification even when a participant has a viral-load measurement.

In general, a threshold-based endpoint gives a direct summary of the share of participants meeting a clinically specified laboratory criterion at a particular time. It is easy to interpret as a response proportion, but it does not retain all the detail in the underlying viral-load values. Participants just above and well above the threshold are grouped together as not meeting the endpoint; participants below the threshold are grouped together as meeting it, subject to the Snapshot rules.

The Full Analysis Set included randomized participants who received at least 1 dose and had at least 1 postbaseline HIV-1 RNA or HBV DNA result while on study drug. The Week 48 endpoint therefore needs to be read in the context of that population definition and the Snapshot classification. The registry describes this as a co-primary endpoint, but another co-primary measure and its result are not reported in the registry record.

7. Results Posted in the Registry

• Blinded Phase: DTG + F/TDF: 91.0% (111/122) versus 95.0% (113/119) on control; risk difference -4.0 percentage points (95% CI -10.4 to 2.5), risk ratio 0.96 (0.89–1.03); unadjusted two-proportion z-test p = 0.228.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 96 as Defined by the US FDA-Defined Snapshot Algorithm

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Blinded Phase: DTG + F/TDF: 87.7% (107/122) versus 87.4% (104/119) on control; risk difference 0.3 percentage points (95% CI -8.0 to 8.6), risk ratio 1.00 (0.91–1.10); unadjusted two-proportion z-test p = 0.942.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Blinded Phase: DTG + F/TDF and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in CD4 Cell Count at Week 48

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Blinded Phase: DTG + F/TDF: mean 175.00 versus 200.00 on control; difference -25.00 (95% CI -58.94 to 8.94), standardized effect d = -0.19; z-test p = 0.149.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Blinded Phase: DTG + F/TDF and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in CD4 Cell Count at Week 96

• 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:
  • Blinded Phase: DTG + F/TDF: mean 229.00 versus 261.00 on control; difference -32.00 (95% CI -76.15 to 12.15), standardized effect d = -0.19; z-test p = 0.155.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Blinded Phase: DTG + F/TDF and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the assessment beyond the Week 48 primary viral-response measure. They include Week 96 viral response, CD4 cell-count changes and CD4 percentage changes at Week 48 and Week 96, hepatitis B DNA response, and ALT normalization. These outcomes address later HIV-1 response, immune measures, and hepatitis-related laboratory measures. The registry lists 12 outcome measures overall and 10 posted secondary outcomes; detailed results are not present for every listed secondary measure.

The posted Week 96 HIV-1 RNA response percentages are 87.4% and 87.7%. The posted CD4 cell-count summaries show positive mean changes in both groups at Week 48 and Week 96. The registry’s ANOVA comparisons for those CD4 outcomes have confidence intervals that include zero. These findings describe different time points and outcome scales from the primary endpoint, and they do not establish that the treatments are equivalent on all outcomes.

In general, secondary outcomes help show whether the pattern across endpoints is coherent and whether the primary result is accompanied by related changes. They do not replace the primary endpoint, which is the outcome designated for the principal trial question. Later assessments can also reflect the follow-up population available at that time; the Week 96 outcome-specific denominators are not the same as the Week 48 primary denominators.

Unadjusted secondary analyses carry less weight because a study may examine multiple outcomes and time points. In general, the more comparisons made, the greater the opportunity for a nominally unusual result to occur by chance. A multiplicity plan can manage that issue, but one is not reported in the registry record. Thus, secondary p-values should be interpreted cautiously and in the context of the prespecified hierarchy, which is not reported. The registry does not provide detailed results for all the hepatitis B and ALT outcomes in the secondary list, so no outcome pattern beyond the posted results can be inferred.

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

• Percentage of Participants With HIV-1 RNA < 50 Copies/mL at Week 96 as Defined by the US FDA-Defined Snapshot Algorithm
• Change From Baseline in CD4 Cell Count at Week 48
• Change From Baseline in CD4 Cell Count at Week 96
• Change From Baseline in Percentage of CD4 Cells at Week 48
• Change From Baseline in Percentage of CD4 Cells at Week 96
• Percentage of Participants With Plasma HBV DNA < 29 IU/mL at Week 96
• Percentage of Participants With Alanine Aminotransferase (ALT) Normalization at Week 48 by American Association for the Study of Liver Diseases (AASLD) Criteria
• Percentage of Participants With ALT Normalization at Week 96

9. Statistical Interpretation

10. Statistical Methods Explained

For the primary endpoint, each group’s outcome is a response proportion: the percentage of participants classified as having HIV-1 RNA < 50 copies/mL at Week 48 by the Snapshot algorithm. The registry reports the arm percentages and also reports a between-group difference in percentages for a non-inferiority analysis. The registry lists a Cochran-Mantel-Haenszel method for its superiority analysis. The specific method for the non-inferiority analysis is not reported in the registry record.

What does the risk difference describe?

In general, a risk difference subtracts one group’s event proportion from the other group’s event proportion. For a response outcome, the “event” is meeting the response definition. A risk difference of zero corresponds to equal response proportions; positive and negative values indicate which group has the higher proportion according to the stated direction of subtraction. The direction matters: the recalculation contrasts DTG + F/TDF with B/F/TAF, whereas the registry-reported non-inferiority difference is presented as B/F/TAF relative to DTG + F/TDF.

The recalculated risk difference is an unadjusted comparison based on the posted summary statistics. It does not apply the registry’s Cochran-Mantel-Haenszel procedure or any adjustment for other variables. The registry’s superiority p-value is tied to its stated Cochran-Mantel-Haenszel analysis; it should not be expected to match the unadjusted p-value from a separate calculation. The registry does not report the stratification variables or further implementation details for that method.

How should a confidence interval be read?

In general, a confidence interval describes the range of values reasonably compatible with the data under the analysis and its assumptions. It communicates precision as well as the direction and possible size of an effect. A narrow interval indicates greater precision than a wide interval on the same scale. An interval that includes zero for a difference does not establish that the groups are identical; it indicates that a zero difference is among the values compatible with that interval. A confidence interval is not a probability statement that the particular fixed effect lies within the calculated limits.

The registry reports a 95.001% interval for the non-inferiority difference and 95% intervals for the secondary contrasts. The unadjusted primary recalculation gives a 95% interval. The confidence level and the exact analysis used should be considered together, especially when comparing the registry’s non-inferiority result with a simple unadjusted recalculation.

What is special about non-inferiority?

In general, a non-inferiority analysis asks whether the response with one treatment is not unacceptably worse than the response with another, using a prespecified margin to define “unacceptably worse.” The test is not simply a conventional test of whether the difference equals zero. The margin determines how much loss is tolerated for the purpose of the analysis, and the interval must be assessed relative to that margin using the specified direction of effect. The margin, its justification, and the full planned non-inferiority procedure are not reported in the registry record. The reported non-inferiority estimate and interval can be quoted, but a reader cannot reconstruct the decision rule from those values alone.

The registry also reports a superiority analysis. In general, a superiority test evaluates whether the data provide evidence of a difference in a specified direction or of any difference, depending on the test definition. It addresses a different inferential question from non-inferiority. A superiority p-value therefore cannot be substituted for the non-inferiority analysis, and a non-significant superiority result does not prove that treatments are equal.

How are the continuous secondary outcomes analyzed?

For CD4 cell count, the posted arm summaries are mean changes from baseline with standard deviations. The recalculated contrasts are unadjusted mean differences based on those summaries. The registry separately reports ANOVA results as differences in least-squares means. A least-squares mean is a model-based estimate, and it need not equal a simple difference between the observed group means. The registry does not report the full ANOVA model specification or its covariates.

For Week 48, the registry reports a least-squares mean difference of 24, with a 95% confidence interval from -10 to 58 and p = 0.170. The simple recalculation gives a mean difference of -25.0 when expressed as DTG + F/TDF relative to B/F/TAF, with an interval from -58.94 to 8.942. The numerical directions differ because the comparison order differs; the registry’s estimate is expressed in the other direction. At Week 96, the registry reports a least-squares mean difference of 30, with a 95% confidence interval from -14 to 74 and p = 0.185. The simple recalculation again uses DTG + F/TDF relative to B/F/TAF. These method-specific estimates should not be conflated.

For binary outcomes, percentages provide a compact summary but discard the exact distribution of continuous measurements. For continuous outcomes, means and standard deviations summarize average change and variability, but do not describe every participant’s trajectory. In general, variability matters because it affects how precisely a group mean or between-group contrast can be estimated. The posted standard deviations help characterize the spread of CD4 change; they do not by themselves reveal the underlying distribution.

What do the planning calculations mean?

The sample-size figures are planning illustrations based on the observed effect, with stated assumptions of a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These calculations are not the trial’s original design justification; that justification is not reported in the registry record. They are also not observed power. Smaller effects require more participants to distinguish the effect from the null with the same planned power, which is why the illustrative requirements increase when the assumed effect is reduced.

In general, power is the probability that a study using a specified design and analysis will reject a null hypothesis when a particular effect is true. A planning calculation specifies a target power before data are collected. It does not show the probability that the observed result is true, and a post hoc calculation based on the observed effect does not measure the strength of evidence independently of the observed estimate and its uncertainty.

Multiplicity also matters when interpreting many outcomes. In general, testing multiple endpoints can increase the chance of at least one false-positive result unless the analysis plan accounts for it. The registry record does not report a multiplicity adjustment or a complete testing hierarchy. Consequently, secondary p-values should be treated as exploratory unless the full prespecified plan indicates otherwise.

11. Confidence Intervals and Precision

The primary response percentages are 95.0% for B/F/TAF and 91.0% for DTG + F/TDF, based on arm counts of 119 and 122. The registry’s non-inferiority estimate is a difference in percentages of 4.1, with a 95.001% confidence interval from -2.5 to 10.8. This interval indicates uncertainty that includes values on both sides of zero. The registry’s non-inferiority conclusion cannot be determined from the interval alone because the margin and full decision rule are not reported in the registry record.

The unadjusted risk-difference recalculation, in the direction DTG + F/TDF relative to B/F/TAF, is -0.040 with a 95% confidence interval from -0.104 to 0.025. This interval also includes zero and extends to values in either direction. Its width reflects uncertainty in the simple unadjusted contrast; it should not be used as though it were the sponsor’s non-inferiority interval or its adjusted superiority analysis.

In general, confidence intervals are more informative than a point estimate alone because they show a range of effect sizes compatible with the data under the analysis. Here, the interval does not support a very precise claim about the exact contrast. It should not be read as proof of equality, and it should not be treated as a range of likely individual participant outcomes. It applies to a group-level difference on the analysis scale.

The registry gives a 95% interval for its Week 48 CD4 least-squares mean contrast from -10 to 58, and a 95% interval at Week 96 from -14 to 74. The unadjusted recalculated intervals are also broad and include zero. These intervals describe average group contrasts, not the range of CD4 changes among individual participants. The means, standard deviations, and model-based estimates answer related but not identical questions.

Precision is also constrained by the analysis population and outcome definition. Snapshot response depends on the viral-load result in the allowed window and discontinuation status. The primary endpoint’s analyzed denominators are not identical to the overall enrollment figure. The registry does not report enough detail to evaluate all missing-outcome handling beyond the stated algorithm and Full Analysis Set definition.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design justification. For the binary outcomes and continuous outcomes shown, the figures are participants per arm; they are not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The assumed effect is the stated fraction of the observed effect. The trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a hypothetical design with an 80% chance of detecting the assumed effect under the stated assumptions, if that effect were the true effect and the analysis followed the calculation’s framework. The 90% power column describes the corresponding planning target with a 90% chance. These are design-planning probabilities, not probabilities that a treatment effect exists and not descriptions of what happened in this completed trial.

Each planning row scales the assumed effect as 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. A smaller assumed effect is harder to distinguish from no difference, so the calculation requires more participants per arm to maintain the same target power. For example, the Week 48 primary illustration at 100% of the observed effect gives 649 participants per arm for 80% power and 868 for 90% power; at 50% of the observed effect, it gives 2,254 and 3,017. These are hypothetical planning quantities, not trial enrollment targets.

The calculations use an observed-effect estimate as their starting point, so their value is illustrative. An observed estimate can be uncertain, and planning around it does not account for every design feature that might have been used in the trial. The original sample-size justification, any design adjustments, and details of the trial’s own power calculation are not reported in the registry record. This is not observed power.

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 = 0.950; treatment proportion p₁ = 0.910; average p̄ = 0.930.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3615 = 0.7086.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3604 = 0.3033.
4. n = (0.7086 + 0.3033)² / (-0.0397)² = 648.3, rounded up to 649 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 <- 0.949579831932773                          # control proportion
p1 <- 0.909836065573771                          # 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(3547908)
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 = 649 (80% power), 868 (90% power)
 75% of observed effect: n per arm = 1,078 (80% power), 1,443 (90% power)
 50% of observed effect: n per arm = 2,254 (80% power), 3,017 (90% power)
power.prop.test: 648.3 
Simulated power at n = 649 per arm: 0.809 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry’s primary result reports the sponsor’s non-inferiority comparison as a difference in percentages of 4.1, with a 95.001% confidence interval from -2.5 to 10.8. It separately reports a Cochran-Mantel-Haenszel superiority analysis with p = 0.211. These are the registry-reported analyses and should take precedence over a simple recalculation when describing the sponsor’s own inferential result.

The unadjusted recalculation uses posted summary statistics to estimate the risk difference for DTG + F/TDF relative to B/F/TAF. Its estimate is -0.040, with a 95% confidence interval from -0.104 to 0.025 and an unadjusted p-value of 0.228. Because the recalculation is unadjusted and uses a different comparison direction, it is not a replication of the sponsor’s analysis. Differences between the p-values can arise because the analyses are not identical; the registry does not report enough detail to identify every reason for the difference.

The registry does not report the non-inferiority margin or the method used for that primary non-inferiority analysis. As a result, the posted non-inferiority estimate and interval can be described, but the decision rule cannot be independently reconstructed from the registry record. The recalculation should be used as a transparent descriptive check, not as a replacement for the sponsor’s prespecified analysis or conclusion.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a Week 48 co-primary endpoint and lists multiple secondary outcomes, including measures assessed at more than one time point. When several outcomes are tested, the interpretation of nominal p-values depends partly on how the testing family and order of tests were prespecified. In general, repeated testing can increase the chance of a false-positive finding if no suitable multiplicity strategy is used. The registry record does not report a multiplicity adjustment, a testing hierarchy, or the complete statistical analysis plan.

The non-inferiority margin for the primary comparison is not reported in the registry record. Neither are the margin’s rationale, the full analysis method for that comparison, or enough detail to reconstruct the sponsor’s decision rule. The registry reports a Cochran-Mantel-Haenszel superiority p-value, but does not report the stratification details. These omissions limit independent evaluation of how the primary analyses were prespecified and implemented.

The primary population is described as the Full Analysis Set: participants randomized, treated with at least 1 dose, and with at least 1 postbaseline HIV-1 RNA or HBV DNA result while on study drug. The endpoint also uses the Snapshot algorithm, which considers viral load in the allowed window and study-drug discontinuation status. The record does not provide a complete accounting of missing Week 48 measurements, reasons for missingness, or sensitivity analyses for missing data. The algorithm’s use is reported, but further details of its implementation are not.

The registry does not report whether the primary result was also evaluated in a per-protocol population or how deviations from assigned treatment were handled in the non-inferiority analysis. In general, population choices can affect non-inferiority interpretation because different analysis populations may have different biases. Without the full protocol and analysis plan, the robustness of the sponsor’s conclusion across analysis populations cannot be assessed from the registry record.

Details of interim analyses, stopping rules, allocation concealment, and the original sample-size justification are also not reported in the registry record. These are not grounds to assume a particular practice; they mark information that cannot be evaluated from the posted registry entries.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: covid-19 (4.9%), haemorrhoids (2.1%), bacterial sepsis (1.1%), groin abscess (1.1%), pneumocystis jirovecii pneumonia (1.1%).

During the blinded phase, serious adverse events were reported for 17 of 121 participants in the B/F/TAF group and 16 of 122 participants in the DTG + F/TDF group. Other adverse events were reported for 102 of 121 and 98 of 122 participants, respectively. The registry also records 2 deaths in the B/F/TAF group and 1 in the DTG + F/TDF group. These are counts in the registry’s adverse-event summaries and should be read alongside the number at risk stated for each group.

In the open-label extension, serious adverse events were reported for 4 of 95 participants continuing from B/F/TAF and 2 of 89 participants continuing from DTG + F/TDF. Other adverse events were reported for 42 of 95 and 40 of 89, respectively. The extension groups represent participants carried forward from different blinded-phase assignments, and these counts are not a randomized comparison of the original groups over a common follow-up period. The registry records 1 death in the extension group continuing from B/F/TAF and none in the group continuing from DTG + F/TDF.

The registry lists Covid-19 (4.9%), haemorrhoids (2.1%), bacterial sepsis (1.1%), groin abscess (1.1%), Pneumocystis jirovecii pneumonia (1.1%), and alcoholic seizure (1.1%) among the top serious-event terms. These terms describe the listed serious events; they do not establish that a study drug caused them. The registry summaries alone do not provide enough information to compare event timing, duration, severity beyond the serious classification, or causality. Safety counts should therefore be interpreted descriptively rather than as proof of a causal difference between regimens.

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

The posted results show that a high percentage of participants in both randomized groups met the Week 48 HIV-1 RNA response definition: 95.0% with B/F/TAF and 91.0% with DTG + F/TDF. The registry reports a non-inferiority estimate and interval, as well as a separate superiority analysis. Those analyses answer different questions and should not be collapsed into a single claim about which regimen is better.

The non-inferiority result must be interpreted against a prespecified margin. Because the margin and full decision rule are not reported in the registry record, the non-inferiority conclusion cannot be independently assessed from the posted numbers alone. The separate superiority p-value is 0.211. It does not provide evidence of superiority under that reported test, but it does not prove equal effects. Likewise, a confidence interval spanning zero is uncertainty about the contrast, not proof that the treatments have identical effects.

The endpoint is a Week 48 threshold-based Snapshot outcome, not a complete account of each participant’s viral-load trajectory. The classification uses the result in a predefined window and study-drug discontinuation status. The observed response proportions therefore describe that endpoint under its algorithm and analysis population, rather than every possible measure of viral control or treatment experience.

The secondary results add information about later viral response and CD4 changes, while the registry also lists hepatitis B and ALT outcomes. The results posted for the later viral and CD4 measures are not interchangeable with the primary endpoint. The registry record does not contain detailed results for every listed secondary outcome, and the multiplicity approach is not reported.

These findings describe one randomized study in treatment-naïve adults with HIV-1 and hepatitis B co-infection. The trial’s completed status and its posted results do not establish how well the findings apply to populations that differ from those described in the record. No conclusion about individual treatment choice follows from group-level statistical results. The evidence reported supports a careful description of observed responses, uncertainty, and limits in the available analysis details—not a medical recommendation.

18. Why This Trial Matters Statistically

This trial is statistically notable because its population combines HIV-1 and hepatitis B co-infection, and its primary endpoint is a threshold-based viral-response measure evaluated with a Snapshot algorithm. The endpoint definition incorporates both a laboratory result at a specified assessment window and study-drug discontinuation status. Understanding that definition is essential before interpreting the response percentages as if they were simple counts of everyone who ever reached a viral-load threshold.

The comparison also illustrates why non-inferiority and superiority are distinct. The registry reports both a non-inferiority estimate and a separate superiority test. The first requires interpretation against a prespecified margin; the second evaluates a different hypothesis. Without the margin and complete planned analysis details, the non-inferiority decision cannot be independently reconstructed. A nonsignificant superiority result cannot fill that gap or demonstrate equivalence.

Differences between a registry-reported model-based or stratified analysis and a simple recalculation are another important statistical lesson. The recalculated primary risk difference is unadjusted and expressed in the reverse direction from the registry’s non-inferiority contrast. It is a useful descriptive check, but not a replacement for the sponsor’s stated analyses. The same principle applies to the CD4 comparisons: simple mean differences and ANOVA least-squares mean differences are related but not identical estimands.

Finally, the results demonstrate the importance of precision, outcome multiplicity, and transparent reporting. Confidence intervals convey uncertainty that point estimates alone obscure. Multiple secondary measures need to be read in light of the analysis hierarchy and any multiplicity handling, neither of which is reported in the registry record. The result is a useful example of why a numerical difference, a p-value, and a non-inferiority claim each need their own statistical 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, its justification, or the complete analysis plan for the primary endpoint. This limits independent assessment of the sponsor’s non-inferiority decision, even though the registry reports its estimate and confidence interval. The registry also identifies a co-primary endpoint without reporting details or results for another co-primary measure.

The posted summary does not provide a full account of missing Week 48 observations, reasons for discontinuation, or sensitivity analyses beyond describing the Snapshot algorithm and Full Analysis Set. It does not report the original sample-size justification, planned interim analyses, or a multiplicity strategy for the many listed outcomes and time points. Therefore, it is not possible to establish from the registry record whether the posted secondary analyses were adjusted or confirmatory.

The recalculated contrasts are unadjusted calculations from summary statistics. They do not reproduce the sponsor’s Cochran-Mantel-Haenszel or ANOVA analyses. The methods and model details for the sponsor’s primary non-inferiority analysis are not reported. Estimates with different adjustment, model, or contrast direction should not be treated as directly interchangeable.

Detailed results are posted for only some of the listed secondary outcomes. The 10 posted secondary outcomes are fewer than the 12 total outcome measures, and the available record does not give enough result information to describe every listed hepatitis B, ALT, or CD4-percentage outcome. The Week 96 and extension summaries also relate to later follow-up populations and should not be read as identical to the primary Week 48 comparison.

Safety summaries provide counts, denominators, selected serious-event terms, and deaths, but do not establish causality or provide full event-level context. The open-label extension counts are not a randomized comparison over a common follow-up period. These limits counsel against treating descriptive adverse-event counts as evidence of a causal safety difference.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy of Bictegravir/Emtricitabine/Tenofovir Alafenamide Versus Dolutegravir + Emtricitabine/Tenofovir Disoproxil Fumarate in Treatment Naive, HIV-1 and Hepatitis B Co-Infected Adults — NCT03547908.
• Registry record last updated 2025-03-19; status last verified 2025-02.
• Results first posted 2023-03-15.
• 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

NCT03547908 is a completed Phase 3, randomized, double-blind, parallel-group study in treatment-naïve adults with HIV-1 and hepatitis B co-infection. The registered enrollment is 244. The blinded comparison was B/F/TAF versus DTG + F/TDF, with matching placebos.

The primary endpoint was the percentage with HIV-1 RNA < 50 copies/mL at Week 48 by the US FDA-defined Snapshot algorithm. The posted percentages were 95.0% and 91.0%. The registry reports a non-inferiority difference of 4.1 with a 95.001% confidence interval from -2.5 to 10.8, and a Cochran-Mantel-Haenszel superiority p-value of 0.211. The non-inferiority margin is not reported in the registry record.

The registry includes Week 96 viral-response and CD4 outcomes, additional listed secondary measures, and adverse-event summaries. The record does not report the complete statistical analysis plan, multiplicity approach, or original sample-size justification. The posted estimates should be interpreted with those reporting limits in mind.