Safety and Efficacy of a Switch to Doravirine, Tenofovir, Lamivudine (MK-1439A) in Human Immunodeficiency Virus (HIV-1)-Infected Participants Virologically Suppressed on an Anti-retroviral Regimen in Combination With Two Nucleoside Reverse Transcriptase Inhibitors (MK-1439A-024): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of a Switch to Doravirine, Tenofovir, Lamivudine (MK-1439A) in Human Immunodeficiency Virus (HIV-1)-Infected Participants Virologically Suppressed on an Anti-retroviral Regimen in Combination With Two Nucleoside Reverse Transcriptase Inhibitors (MK-1439A-024) (NCT02397096), a randomized phase 3 study. The primary outcome is Percentage of Participants Maintaining Human Immunodeficiency Virus-1 Ribonucleic Acid (HIV-1 RNA) <50 Copies/mL.

2. Clinical Question

3. Trial Design

This was a Phase III, multicenter, randomized, open-label study with a parallel-group design. The registry lists enrollment of 673 and identifies Merck Sharp & Dohme LLC as the sponsor. The study is marked completed. Start and primary completion dates are recorded as 2015-06-09 and 2018-02-22, respectively. These registry entries describe the study record and do not by themselves establish how completely outcomes were collected or reported.

The comparison was between an immediate switch to doravirine, tenofovir, and lamivudine and a delayed switch. The immediate-switch group is reported at Week 48 for the primary endpoint; the delayed-switch group is reported at Week 24. Thus, the primary comparison does not represent the same duration on the switched regimen in both groups. The delayed group serves as a continuation-regimen comparison during the earlier period, then has a later switch. The study’s brief description says Base Study results are based on the first 48 weeks of an ongoing study.

The posted primary analysis population is described as all randomized participants who received at least one dose of study drug. The outcome used the FDA “snapshot” approach, with missing data counted as treatment failures regardless of reason. The primary outcome is the proportion maintaining HIV-1 RNA below 50 copies/mL. The registry also reports secondary virologic outcomes, CD4 cell-count changes, and fasting lipid changes, alongside adverse-event information.

Details of the randomization procedure, allocation concealment, stratification, protocol deviations, and the original sample-size rationale are not reported in the registry record. Open-label status means treatment assignment was not masked, but the record does not explain whether outcome assessment involved any additional safeguards. These missing details limit assessment of the design beyond the randomized, parallel comparison that is explicitly described.

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: Out of 852 participants screened, 673 were randomized to study treatment, and 670 were treated. There were 122 global study sites utilized.

Day 1 to Week 24

Reasons for not completing this period:

Week 24 to Week 48

Reasons for not completing this period:

Study Extension 1

Reasons for not completing this period:

Study Extension 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants who received at least 1 dose of study drug.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Maintaining Human Immunodeficiency Virus-1 Ribonucleic Acid (HIV-1 RNA) <50 Copies/mL, measured over Immediate Switch to MK-1439A arm: Week 48; Delayed Switch to MK-1439A arm: Week 24.

The primary endpoint is the percentage of participants maintaining HIV-1 RNA below 50 copies/mL. It represents the proportion in each group whose measured plasma viral RNA was below the stated threshold at the relevant assessment. The registry specifies the Abbott RealTime HIV-1 Assay and says the endpoint was evaluated using the FDA “snapshot” approach. Under the posted handling rule, missing outcome data were treated as treatment failures, whatever the reason for missingness.

This type of endpoint is useful in a switch study because it asks whether virologic suppression is maintained after changing an established regimen, rather than focusing only on a change in a laboratory average. The threshold defines the outcome being counted; a participant either meets the stated endpoint criterion or does not. That makes the group result a percentage, and differences between groups can be expressed as differences in the proportions meeting the criterion.

The registry’s primary hypothesis was non-inferiority: the switch strategy was to be evaluated against continuation of the baseline regimen, with the stated goal of preserving suppression. Non-inferiority is not established solely because group percentages look similar or because an interval includes no difference. Interpretation requires a prespecified margin defining how much worse the new strategy could be while still meeting the study’s criterion. That margin is not reported in the registry record.

The primary outcome’s timeframes are not identical: the immediate-switch group is listed at Week 48 and the delayed-switch group at Week 24. This timing should be kept in view when interpreting the comparison. The record does not provide enough information to determine whether additional analyses addressed the difference in follow-up exposure.

7. Results Posted in the Registry

• Delayed Switch Group (DSG): 94.6% (211/223) versus 90.8% (406/447) on control; risk difference 3.8 percentage points (95% CI -0.2 to 7.8), risk ratio 1.04 (1.00–1.09); unadjusted two-proportion z-test p = 0.087.

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 Maintaining HIV-1 RNA <50 Copies/mL

• 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:
  • Delayed Switch Group (DSG): 94.6% (211/223) versus 93.7% (419/447) on control; risk difference 0.9 percentage points (95% CI -2.8 to 4.6), risk ratio 1.01 (0.97–1.05); unadjusted two-proportion z-test p = 0.649.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Delayed Switch Group (DSG) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Maintaining HIV-1 RNA <40 Copies/mL

• 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:
  • Delayed Switch Group (DSG): 93.3% (208/223) versus 89.7% (401/447) on control; risk difference 3.6 percentage points (95% CI -0.8 to 7.9), risk ratio 1.04 (0.99–1.09); unadjusted two-proportion z-test p = 0.131.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Delayed Switch Group (DSG) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With HIV-1 RNA >=50 Copies/mL

• 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:
  • Delayed Switch Group (DSG): 1.8% (4/223) versus 1.6% (7/447) on control; risk difference 0.2 percentage points (95% CI -1.9 to 2.3), risk ratio 1.15 (0.34–3.87); unadjusted two-proportion z-test p = 0.827.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Delayed Switch Group (DSG) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary question in several directions: maintenance of the RNA suppression threshold at another assessment time, maintenance below a different RNA threshold, RNA at or above the stated threshold, CD4 cell-count change, and fasting lipid changes. The posted secondary results therefore include both virologic endpoints and laboratory measures, rather than a single family of interchangeable outcomes.

Across the secondary virologic comparisons, both groups have high observed maintenance percentages, and the unadjusted intervals do not give a clear separation between groups. This is broadly consistent with the primary result’s pattern of high suppression in both groups and uncertainty around the difference. The secondary results are supportive context, not an independent confirmation of the primary non-inferiority claim. They have different endpoint definitions and, in some cases, different follow-up times.

Secondary findings generally carry less weight than the primary endpoint for the main study question because they are not the central comparison specified in the stated hypothesis. When many outcomes are examined, the chance of observing an apparently notable result by chance can increase. General statistical principle: multiplicity procedures or a prespecified hierarchy can address that issue, but the registry does not report such a plan. The record also does not report adjusted secondary p-values or a multiplicity strategy.

Accordingly, secondary estimates are best read as descriptive and exploratory unless the full analysis plan establishes otherwise. They may help characterize the wider outcome profile, but they do not remove the need to consider the primary endpoint’s different timeframes, non-inferiority margin, and missing-data handling. No overall conclusion about every secondary measure can be drawn from the registry record where a result or analysis detail is not reported.

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

• Mean Change From Baseline in Fasting Low-density Lipoprotein Cholesterol (LDL-C)
• Mean Change From Baseline in Fasting Non-high-density Lipoprotein Cholesterol (Non-HDL-C)
• Percentage of Participants Maintaining HIV-1 RNA <50 Copies/mL
• Mean Change From Baseline in Cluster of Differentiation (CD4) Cell Counts
• Mean Change From Baseline in Cluster of Differentiation (CD4) Cell Counts
• Percentage of Participants Maintaining HIV-1 RNA <40 Copies/mL
• Percentage of Participants Maintaining HIV-1 RNA <40 Copies/mL
• Percentage of Participants With HIV-1 RNA >=50 Copies/mL

9. Statistical Interpretation

10. Statistical Methods Explained

What does a percentage endpoint represent?

The primary outcome is binary at the participant level: the measured HIV-1 RNA either falls below the specified threshold at assessment or it does not. A group percentage summarizes the proportion meeting that criterion. A risk difference, also called a difference in proportions, subtracts the outcome proportion in one group from the proportion in the other. The recalculated contrast is oriented as delayed switch minus immediate switch. A positive estimate therefore corresponds to a higher observed proportion in the delayed-switch group. This orientation is a matter of definition; it does not itself indicate which group is preferable.

The primary group estimates are percentages, while the recalculated difference and its interval are on a proportion scale. The sponsor-reported treatment difference is presented on a percentage-point scale. These are different presentations of a comparison of the same general endpoint, but details of the sponsor’s exact analysis method are not reported in the registry record. The recalculation is an unadjusted calculation from posted summary statistics, not an adjusted model or an individual-participant analysis.

How should confidence intervals and p-values be read?

A confidence interval describes the range of effect estimates reasonably compatible with the observed data under the statistical procedure used. Wider intervals indicate less precision; intervals that cross zero do not establish a directional difference at the conventional two-sided significance threshold. Crossing zero does not demonstrate that groups are equivalent. A non-significant result can reflect uncertainty, and the interval should be considered alongside the clinical question and analysis plan.

The unadjusted p-value is a measure of how unusual data at least as discordant with a no-difference assumption would be under that assumption and the calculation’s statistical model. It is not the probability that the treatments are the same, and it is not a measure of the size or clinical importance of an effect. The sponsor’s posted analysis has no p-value listed. The record’s primary hypothesis is non-inferiority, which is assessed against a specified margin rather than by relying on a test of no difference alone.

What is special about non-inferiority?

In a non-inferiority analysis, the study asks whether the new strategy is not worse than the comparator by more than an acceptable prespecified amount. The margin is essential: it defines the maximum difference that would still count as non-inferior. The registry describes a non-inferiority hypothesis but does not report the margin. Without it, a reader cannot apply the decision rule to the sponsor’s interval. The record also does not report the full protocol statistical plan, including the details needed to establish whether all prespecified non-inferiority analyses were conducted as planned.

Non-inferiority studies can be sensitive to departures from the planned design and to missing outcomes. The posted analysis counts missing data as failures, which is a stated approach, but the registry record does not provide further details about reasons for missingness or sensitivity analyses. It is therefore not possible to judge from this record alone how robust the result is to alternative assumptions about missing outcomes.

Why do the timeframes matter?

The primary result compares the immediate-switch group at Week 48 with the delayed-switch group at Week 24. A direct difference in percentages can be calculated from the posted summaries, but the groups are assessed at different points in their treatment course. The Week 48 result for the immediate-switch group reflects a longer time after switching than the Week 24 result for the delayed-switch group. The registry’s planned description says the primary hypothesis concerns non-inferiority at 24 weeks; the posted primary endpoint, however, lists the different group timeframes. The registry does not report enough detail to establish how the sponsor’s analysis handled this distinction.

What does the missing-data rule do?

The FDA snapshot approach classifies participants according to their status at a defined assessment, and the record states that all missing data were treated as treatment failures regardless of reason. This means the reported percentage is not simply the fraction of participants with an available laboratory result who were suppressed. The rule incorporates missingness into the outcome definition. It avoids treating missing participants as successes, but it also means the percentage can be affected by attendance, discontinuation, or data availability. The record does not report a breakdown of missingness or alternative analyses.

Why are recalculations and sponsor results distinguished?

The recalculated comparison uses the posted arm-level proportions and counts and is unadjusted. It is useful for a transparent summary of the observed group contrast, but it may not reproduce an analysis that uses a prespecified estimand, covariates, stratification, or other design features. The registry does not report the method for the sponsor’s treatment-difference analysis. The two presentations should therefore be read as related but not automatically identical statistical procedures. In this record, the recalculation does not establish a different conclusion from the sponsor’s report; the exact relationship between their methods cannot be determined from the posted description.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.038, with a 95% confidence interval from -0.002 to 0.078. This interval is relatively broad around the estimate and crosses zero. It is compatible with a small difference favoring the immediate-switch group as well as a larger difference favoring the delayed-switch group, within the bounds stated by the interval. The interval communicates uncertainty about the magnitude and direction of the contrast; it does not assign probabilities to particular treatment effects.

The sponsor-reported treatment difference is -3.784, with a 95% confidence interval from -7.877 to 0.310. This is a separate reported interval on a percentage-point scale. It also crosses zero. Although the two intervals are expressed differently, both indicate uncertainty around the direction of the observed contrast. Neither interval should be interpreted as proof that the strategies are equivalent.

Precision is affected by the amount of information available and by how common the endpoint is. General statistical principle: estimates from binary outcomes depend on the observed proportions and the number of observations; less information generally yields wider uncertainty intervals. The reported group sizes are 447 and 223, and the result counts are 406 and 211 meeting the primary criterion. These counts underpin the displayed group estimates, but the posted outcome definition also treats missing outcomes as failures.

The precision question for non-inferiority is not just whether the interval crosses zero. The interval must be compared with the prespecified non-inferiority margin, and that margin is not reported in the registry record. The different assessment times for the immediate- and delayed-switch groups further limit how directly the intervals answer a common-time comparison. The posted information allows the interval’s width and direction to be described, but not a definitive judgment against the non-inferiority criterion.

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 describe participants per arm, not a total across the study. They use the observed effect as a starting point and show planning for 100%, 75%, and 50% of that observed effect. For each effect assumption, the displayed columns correspond to planning for 80% power and 90% power. In plain language, those power levels describe the probability of detecting the chosen effect under the stated planning assumptions if that effect is present; they do not describe the probability that the trial’s conclusion is correct.

The planning assumptions listed in the registry-derived calculation are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The trial’s original design assumptions and sample-size justification are not reported in the registry record, so these calculations should not be taken as a reconstruction of the study’s original plan.

The illustrations show that smaller effects require more participants per arm to reach the same target power. For example, planning for 50% of the observed primary effect requires 3,297 participants per arm for 80% power and 4,413 participants per arm for 90% power, compared with 736 and 985 when planning for 100% of the observed effect. These are planning illustrations, not observed power. The displayed assumptions are hypothetical planning choices, and the calculations do not establish what effect a future study would actually observe.

The sample-size curve should be read as a visual expression of the same relationship between assumed effect size and required participants per arm. It is not a result from the randomized trial and does not represent an additional clinical finding.

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 = 0.908; treatment proportion p₁ = 0.946; average p̄ = 0.927.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3673 = 0.7200.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3664 = 0.3083.
4. n = (0.7200 + 0.3083)² / (0.0379)² = 735.8, rounded up to 736 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 <- 0.9082774049217                          # control proportion
p1 <- 0.946188340807175                          # 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(2397096)
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 = 736 (80% power), 985 (90% power)
 75% of observed effect: n per arm = 1,388 (80% power), 1,857 (90% power)
 50% of observed effect: n per arm = 3,297 (80% power), 4,413 (90% power)
power.prop.test: 735.8 
Simulated power at n = 736 per arm: 0.806 (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-reported primary result is a treatment difference of -3.784 with a 95% confidence interval from -7.877 to 0.310. The registry labels this analysis as non-inferiority. The interval crosses zero, and the registry record does not state the non-inferiority margin or give a p-value for this analysis. Without the margin, the reported result cannot be independently checked against the study’s non-inferiority decision rule using the registry record alone.

The unadjusted recalculation from the posted group summaries gives a risk difference of 0.038, with a 95% confidence interval from -0.002 to 0.078, oriented as delayed switch minus immediate switch. Its presentation differs from the sponsor’s treatment difference: the signs reflect the contrast’s direction and the scales differ. The two results describe a similar broad pattern of uncertainty around the group contrast, but the record does not provide enough detail about the sponsor’s analysis method to establish that the estimates are exactly interchangeable.

The recalculation is a transparent summary based on arm-level results, not a replacement for the sponsor’s analysis. The record marks the discrepancy indicator as false, so there is no flagged conflict between the posted sponsor result and the recalculated summary. Details such as adjustment choices and the exact estimand for the sponsor’s calculation are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry describes a primary non-inferiority hypothesis and lists multiple secondary outcomes. It does not report a multiplicity adjustment, a testing hierarchy, or whether secondary outcomes were designated as confirmatory or exploratory. This matters because examining multiple outcomes can make chance findings more likely. Without a stated strategy, secondary p-values and confidence intervals should not be treated as if each arose from a single prespecified test.

The record’s primary endpoint description gives an explicit missing-data rule: the FDA snapshot approach was used, and missing data were considered treatment failures regardless of the reason. This makes the handling rule interpretable, but the record does not provide missing-data counts, reasons, or sensitivity analyses using different assumptions. Missingness can affect the group percentages, particularly if data availability differs between groups or is related to outcome status. The record does not provide enough information to assess those possibilities.

The primary population is defined as all randomized participants who received at least one dose of study drug. That is the population stated for the posted primary endpoint, but the record does not describe additional analysis populations or provide a comparison of results across them. Details of protocol deviations, treatment discontinuation, adherence, and analysis-population exclusions are not reported in the registry record.

Other important analysis-plan details are also not reported in the registry record, including the non-inferiority margin, the full statistical method for the sponsor’s treatment difference, and the original sample-size justification. The record does not report whether interim analyses were planned or conducted. These omissions do not change the posted numerical results, but they limit independent evaluation of how the confirmatory decision was specified and whether all analyses followed the prespecified plan.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: tendon rupture (2.3%), pneumonia (1.3%), covid-19 (1.2%), bowen's disease (1.2%), nephrolithiasis (1.2%).

The registry reports serious adverse events and other adverse events in several study periods, separately for the immediate- and delayed-switch groups. For the Base Study Weeks 0-24 period, serious adverse events affected 13 participants in the immediate-switch group and 8 in the delayed-switch group. In the Base Study Weeks 24-48 period, the corresponding counts are 11 and 4. Later extension periods are reported separately, with the number at risk varying by period. These are period-specific figures; they should not be added together to create a participant total because the record does not establish whether the same participant could appear in more than one period.

The registry also lists deaths by period, including one in the immediate-switch group during Base Study Weeks 0-24 and one during Study Extension 1, with no deaths listed for the other reported periods. The listed serious-event terms include tendon rupture, pneumonia, COVID-19, Bowen's disease, nephrolithiasis, and appendicitis, each with its recorded percentage. These term percentages do not replace the group-level event counts, and the registry does not provide enough information to infer causality or compare risks for individual terms.

Safety figures are descriptive counts across periods with changing numbers at risk. They should be read separately from the efficacy endpoint and do not establish that an event was caused by a study regimen.

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

The posted results show that a high percentage of participants in each group met the HIV-1 RNA threshold at the reported assessment. The primary percentages are 90.8% for the immediate-switch group at Week 48 and 94.6% for the delayed-switch group at Week 24. The observed contrast and its confidence interval indicate uncertainty about the size and direction of the difference. The primary sponsor analysis is labelled non-inferiority, but the registry record does not report the margin needed to interpret that claim independently.

These findings do not establish that the regimens are equivalent. A failure to show a clear difference is not the same as demonstrating that any difference is sufficiently small. It also does not establish what would happen in populations or settings not described by this study. The record concerns people with HIV-1 who were already virologically suppressed on antiretroviral therapy and were randomized to immediate or delayed switching; it is not a study of treatment initiation in people without established therapy.

The outcomes should be interpreted in light of the unequal assessment times between groups, the snapshot rule that counts missing outcomes as failures, and the absence of details about missingness and sensitivity analyses. The registry record also lacks the non-inferiority margin and parts of the original statistical plan. Those are important limits on a definitive interpretation.

The data describe observed group outcomes and serious adverse-event reporting over the study periods. They do not, by themselves, prove that one regimen is safer or more effective, explain the cause of an adverse event, or support medical advice. Clinical decisions require consideration of a person’s circumstances and evidence beyond the registry results.

18. Why This Trial Matters Statistically

This trial illustrates why interpretation of a randomized comparison depends on more than comparing two percentages. The primary hypothesis is non-inferiority, so the decision depends on a prespecified margin as well as the estimated difference and its uncertainty. The registry reports the sponsor’s treatment difference and interval, but not the margin. A reader can describe the result without being able to reproduce the study’s non-inferiority decision rule.

The timing also matters. The immediate-switch group’s primary result is reported at Week 48, while the delayed-switch group’s is reported at Week 24. The numbers therefore relate to different follow-up points in the switch sequence, even though they are presented as the primary comparison. This makes careful reading of the outcome timeframe central to understanding what contrast the result represents.

The endpoint is a threshold-based binary outcome, and missing data are treated as failures under the stated snapshot approach. That rule has a direct effect on what the group percentages mean. It also demonstrates why an analysis population and missing-data strategy should be considered alongside the efficacy estimate, not as administrative details separate from the result.

Finally, the record distinguishes sponsor-reported analysis from an unadjusted recalculation from arm summaries. The recalculation makes the basic group contrast transparent, while the sponsor result is the reported analysis for the stated non-inferiority hypothesis. The record does not supply all methodological details needed to treat them as identical. These features make the trial a useful example of how estimand, timing, missingness, and uncertainty jointly shape interpretation.

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.

A key limitation for independent interpretation is that the registry does not report the non-inferiority margin. The primary hypothesis is explicitly non-inferiority, but the margin is essential for deciding whether the confidence interval meets the intended criterion. The sponsor analysis is reported as a treatment difference with a confidence interval, yet the decision threshold cannot be checked from the registry record alone.

The primary endpoint lists different follow-up times for the groups: Week 48 for immediate switch and Week 24 for delayed switch. This complicates a simple interpretation of the between-group contrast as if it represented the same period after switching. The registry does not provide further explanation of the analysis’s handling of this difference.

The record states that missing data were counted as failures, but it does not report the amount or reasons for missingness or sensitivity analyses. It also does not report the full statistical analysis plan, the randomization procedure, allocation concealment, stratification, or the original sample-size justification. The sponsor’s analysis method is not specified in the posted result.

Other limitations include the open-label design and the variety of secondary outcomes. The record does not report whether outcome assessment was blinded or whether secondary testing was adjusted for multiplicity. The study population is described as virologically suppressed participants receiving established antiretroviral regimens; the registry record does not support extending the results beyond that described population. Safety reporting is divided across periods, and the listed event figures should not be combined into totals without participant-level information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy of a Switch to Doravirine, Tenofovir, Lamivudine (MK-1439A) in Human Immunodeficiency Virus (HIV-1)-Infected Participants Virologically Suppressed on an Anti-retroviral Regimen in Combination With Two Nucleoside Reverse Transcriptase Inhibitors (MK-1439A-024) — NCT02397096.
• Registry record last updated 2024-11-20; status last verified 2024-11.
• Results first posted 2019-04-03.
• 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 NCT02397096 as a completed Phase III, multicenter, randomized, open-label, parallel study sponsored by Merck Sharp & Dohme LLC. It enrolled 673 and compared an immediate switch to doravirine, tenofovir, and lamivudine with a delayed switch among participants with HIV-1 who were virologically suppressed on antiretroviral therapy.

The primary endpoint was maintenance of HIV-1 RNA below 50 copies/mL. The posted percentages are 90.8% for the immediate-switch group at Week 48 and 94.6% for the delayed-switch group at Week 24. The record reports a sponsor treatment difference of -3.784 with a 95% confidence interval from -7.877 to 0.310, and an unadjusted recalculation of 0.038 with a 95% confidence interval from -0.002 to 0.078, oriented as delayed switch minus immediate switch.

The registry identifies the primary hypothesis as non-inferiority but does not report the margin. The different assessment times and the stated missing-data-as-failure rule are important to interpretation. Secondary outcomes and safety information provide additional descriptive context, but the record does not report all details needed for independent evaluation of the full statistical plan.