Safety and Efficacy of Doravirine (MK-1439) in Participants With Human Immunodeficiency Virus 1 (HIV-1) (MK-1439-018): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Doravirine (MK-1439) in Participants With Human Immunodeficiency Virus 1 (HIV-1) (MK-1439-018) (NCT02275780), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving Plasma HIV-1 RNA <50 Copies/mL at Week 48.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, double-blind, active-comparator-controlled, parallel-group trial in treatment-naïve participants with HIV-1. Doravirine 100 mg once daily was compared with darunavir 800 mg plus ritonavir 100 mg once daily. Each regimen was given with an investigator-selected TRUVADA™ or EPZICOM™/KIVEXA™ backbone. The registry lists enrollment as 769 and the study status as completed.

The Base Study was planned to provide double-blind treatment for 96 weeks. Eligible participants in either group could continue into an open-label extension receiving a doravirine-containing regimen. A further extension was described for eligible participants deriving benefit, continuing until doravirine became locally available or for an additional 96 weeks, whichever came first. These extension descriptions do not change the randomized Week 48 primary comparison, which is the principal focus of the primary result.

The primary endpoint was the percentage of participants with HIV-1 RNA <50 copies/mL at Week 48. The registry summary identifies non-inferiority as the primary hypothesis, with superiority to be assessed if non-inferiority was established. The record also lists Week 96 virologic response, CD4+ T-cell changes, and fasting lipid changes among secondary outcomes. The posted results include several additional HIV-1 RNA thresholds and follow-up times.

The primary endpoint population is described as randomized participants who received at least 1 dose of study drug, and missing data were handled using the FDA snapshot approach, with every missing value treated as treatment failure regardless of reason. The original design assumptions, including any sample-size justification, are not reported in the registry record. Randomization and masking describe design features, but the registry entries do not establish how allocation was generated or concealed.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: A total of 1027 participants were screened and 769 were randomized.

Base Study: 96 Weeks

Reasons for not completing this period:

Study Extension 1: Week 96 to Week 192

Reasons for not completing this period:

Study Extension 2: Week 192 to Week 288

Reasons for not completing this period:

Study Extension 3: Week 288 to Week 384

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 Achieving Plasma HIV-1 RNA <50 Copies/mL at Week 48, measured over Week 48.

The primary endpoint measures the proportion of participants whose plasma HIV-1 RNA was below 50 copies/mL at Week 48. Viral RNA was quantified using the Abbott RealTime HIV-1 Assay. The registry describes this as a binary response: each participant is classified according to whether the threshold was reached or not. Missing data were counted as treatment failures under the stated FDA snapshot approach.

This endpoint is used to summarize virologic response at a specified follow-up time. In general, a threshold-based endpoint can make a trial question clinically and statistically concrete: the analysis compares how often participants in each group meet the prespecified threshold, rather than comparing only average RNA values. The registry’s choice of the Week 48 threshold is tied to its stated primary hypothesis of non-inferiority. The registry summary says that superiority would be evaluated only if non-inferiority were established.

In the posted primary results, the response percentages are 83.8 for doravirine and 79.9 for darunavir plus ritonavir. These percentages describe the endpoint as handled in the registry, including its missing-data rule. They do not, by themselves, establish the trial’s formal non-inferiority conclusion. The non-inferiority margin and the details needed to assess that criterion are not reported in the registry record.

The endpoint also does not describe every aspect of participant experience, safety, or longer-term outcomes. Those require separate results and interpretation. A single threshold at one follow-up time is informative for the stated question, but it is not a complete account of all outcomes in the trial.

7. Results Posted in the Registry

• Daurunavir 800 mg + Ritonavir 100 mg: 79.9% (306/383) versus 83.8% (321/383) on control; risk difference -3.9 percentage points (95% CI -9.4 to 1.5), risk ratio 0.95 (0.89–1.02); unadjusted two-proportion z-test p = 0.160.

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 Achieving Plasma HIV-1 RNA <50 Copies/mL at Week 96

• 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:
  • Daurunavir 800 mg + Ritonavir 100 mg: 66.0% (248/376) versus 73.1% (277/379) on control; risk difference -7.1 percentage points (95% CI -13.7 to -0.6), risk ratio 0.90 (0.82–0.99); unadjusted two-proportion z-test p = 0.033.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Daurunavir 800 mg + Ritonavir 100 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Achieving Plasma HIV-1 RNA <40 Copies/mL at Week 48

• 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:
  • Daurunavir 800 mg + Ritonavir 100 mg: 79.1% (303/383) versus 83.3% (319/383) on control; risk difference -4.2 percentage points (95% CI -9.7 to 1.3), risk ratio 0.95 (0.89–1.02); unadjusted two-proportion z-test p = 0.139.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Daurunavir 800 mg + Ritonavir 100 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Achieving Plasma HIV-1 RNA <40 Copies/mL at Week 96

• 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:
  • Daurunavir 800 mg + Ritonavir 100 mg: 64.4% (242/376) versus 72.0% (273/379) on control; risk difference -7.7 percentage points (95% CI -14.3 to -1.0), risk ratio 0.89 (0.81–0.99); unadjusted two-proportion z-test p = 0.024.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Daurunavir 800 mg + Ritonavir 100 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary virologic outcomes follow a broadly consistent descriptive pattern: the reported response percentage is higher in the doravirine group for the listed Week 96 HIV-1 RNA <50 copies/mL outcome and for the <40 copies/mL outcomes at Weeks 48 and 96. The posted recalculated comparisons for these endpoints are unadjusted. Their estimates and intervals are presented with the endpoint results, and they should be read as supporting context rather than as replacements for the primary Week 48 endpoint.

These results relate to the primary finding because they use related viral RNA response definitions at a different threshold or follow-up time. Agreement in direction across related measures can add descriptive coherence, but it does not prove that the primary non-inferiority criterion was met or establish a separate confirmatory conclusion. The registry’s stated primary question remains the Week 48 <50 copies/mL non-inferiority comparison, and its margin is not reported in the registry record.

The registry also lists CD4+ T-cell and fasting lipid outcomes among secondary measures, but numerical results for those outcomes are not reported in the record. The registry identifies 15 posted secondary outcomes, while the endpoint-specific results available in the posted material include the three virologic results. The other secondary outcome values and their analysis details are not reported in the registry record.

Multiplicity is important because assessing many outcomes creates more opportunities for chance findings. Unless a prespecified adjustment or testing hierarchy controls that risk, individual unadjusted secondary results carry less weight than a primary result tested under its stated plan. The registry record does not report a multiplicity adjustment or a complete testing hierarchy. Accordingly, secondary patterns are useful for context, but they should not be treated as independent proof of a treatment difference.

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

• Percentage of Participants Achieving Plasma HIV-1 RNA <50 Copies/mL at Week 96
• Change From Baseline in Mean CD4+ T-cell Count at Week 48
• Change From Baseline in Mean CD4+ T-cell Count at Week 96
• Mean Change From Baseline in Fasting Low Density Lipoprotein Cholesterol (LDL-C) at Week 48
• Mean Change From Baseline in Fasting Non-High Density Lipoprotein Cholesterol (Non-HDL-C) at Week 48
• Mean Change From Baseline in Fasting High Density Lipoprotein Cholesterol (HDL-C) at Week 48
• Mean Change From Baseline in Fasting Total Cholesterol at Week 48
• Mean Change From Baseline in Fasting Triglyceride at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: a participant either meets the HIV-1 RNA threshold at the specified follow-up or does not. For a binary outcome, the group percentage gives the observed response frequency among the analysis population described by the registry. The primary results report 83.8% for doravirine and 79.9% for darunavir plus ritonavir at Week 48. The percentages are the clearest direct description of the arm-level outcome, while a difference measure summarizes the contrast between groups.

What does the recalculated risk difference represent?

The recalculated risk difference is expressed as comparator minus doravirine. At Week 48, it is -0.039. This subtraction convention makes a negative value correspond to a lower response proportion in the comparator group. That is consistent with the posted arm percentages, where the comparator percentage is lower. A risk difference is an absolute contrast on the probability scale; it is not a relative ratio and should not be read as a percent change.

The recalculation uses the posted summary counts and proportions without adjustment. It is therefore a simple unadjusted comparison, not necessarily the same estimator, population handling, or model used by the sponsor. The reported result and the recalculated result answer related questions but should not be treated as interchangeable. The registry indicates no discrepancy flag, but the reported analysis remains the sponsor’s designated analysis for the trial’s formal non-inferiority question.

How should the confidence interval be read?

A confidence interval communicates uncertainty around an estimated contrast. In general, it describes a range of values compatible with the observed data under the method used, with a stated confidence level. The recalculated Week 48 risk-difference interval is -0.094 to 0.015. Because this interval includes zero, it does not clearly distinguish a difference from no difference using a conventional two-sided difference interpretation. It also includes values on either side of zero, so the data are compatible with more than one direction of effect.

Confidence intervals do not give the probability that a particular treatment effect is true, and they do not resolve the separate non-inferiority question. A non-inferiority analysis compares an interval or test statistic with a prespecified margin. The margin is not reported in the registry record. Without it, the interval cannot be used to independently verify a non-inferiority conclusion.

What is the role of the unadjusted p-value?

The primary recalculation reports an unadjusted p-value of 0.16. In general, a p-value measures how unusual the observed result, or a more extreme result, would be under a specified null hypothesis and analysis procedure. It is not the probability that the null hypothesis is true, and it is not a measure of effect size. The p-value accompanies an unadjusted test of a difference and does not replace the trial’s non-inferiority framework. The sponsor-reported primary analysis has no p-value listed in the registry record.

“Unadjusted” matters because the calculation does not account for other endpoints or comparisons. If many outcomes are examined, some may appear more notable by chance. A multiplicity strategy can address that issue, but one is not reported in the registry record. Thus the secondary p-values should be read as exploratory evidence rather than as a collection of independent confirmatory tests.

Why is non-inferiority distinct from superiority?

In general, a non-inferiority trial asks whether the new regimen’s outcome is not unacceptably worse than the comparator, according to a prespecified margin. A superiority test asks whether one regimen performs better according to a specified statistical criterion. These are distinct questions and use different decision references. The registry states that doravirine was to be tested for non-inferiority first and that superiority would be assessed if non-inferiority were established. The margin, testing details, and a clear formal conclusion are not reported in the registry record. An unadjusted difference test should therefore not be used to infer the result of that sequence.

How does missing-data handling affect the endpoint?

The registry says it used the FDA snapshot approach and counted all missing data as treatment failures, regardless of the reason. This is an explicit rule for the primary endpoint and means that missingness affects the response classification rather than being omitted from the endpoint definition. In general, treating missing outcomes as failures can make the estimated response proportion lower than an approach that excludes missing observations, but the size and direction of any difference depend on the missing data pattern. The record does not report how many outcomes were missing or provide alternative analyses.

The primary population is described as randomized participants who received at least 1 dose of study drug. That description is narrower than all randomized participants, and it should be kept in mind when interpreting the result. The registry does not report additional sensitivity analyses or enough detail to reconstruct the sponsor’s full statistical procedure.

11. Confidence Intervals and Precision

The recalculated Week 48 risk difference is -0.039, with a 95% confidence interval from -0.094 to 0.015. Its width indicates that the point estimate is not highly precise: the data remain compatible with a range of possible contrasts, including values on both sides of zero. In general, greater precision corresponds to a narrower interval, while a wider interval signals more uncertainty about the size and direction of the underlying difference.

The arm percentages provide context for the estimate: 83.8% achieved the threshold in the doravirine group and 79.9% in the comparator group. These are observed summaries, not exact values for the broader population. The confidence interval is the key uncertainty measure for the contrast, but it is tied to the recalculation method and should not be mistaken for the sponsor’s formal non-inferiority analysis.

The sponsor-reported treatment difference is 3.913, with a 95% confidence interval from -1.590 to 9.415. Its interval also includes zero. The sponsor’s scale and contrast direction differ from the simple recalculation, so the two intervals should not be compared as if they were estimates using an identical method. Neither interval alone identifies the non-inferiority margin or proves that the formal criterion was met.

Confidence intervals describe statistical uncertainty, not all uncertainty. They do not capture possible limitations from missing information, outcome definitions, or the degree to which the trial population represents other settings. The registry does not report the original sample-size assumptions, the non-inferiority margin, or a complete analysis specification. Those omissions constrain a full appraisal of precision and formal decision-making.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial’s original design calculations. For this binary endpoint, figures are participants per arm, rather than total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The column for 80% power gives the estimated number of participants per arm under those assumptions for a study to have an 80% chance of detecting the chosen effect if that effect is the true one. The column for 90% power describes the corresponding planning target for a 90% chance. Power is a design concept tied to a particular assumed effect, analysis, and significance level; it is not a property that can be read directly from the observed trial result.

The rows reduce the effect used for planning from 100% to 75% to 50% of the observed effect. The participant requirements increase as the assumed effect gets smaller. This is expected in general: smaller group differences are harder to distinguish from random variation, so more participants are needed to achieve the same planned power under otherwise unchanged assumptions.

For the primary Week 48 endpoint, the illustration lists 1,519 participants per arm for 80% power and 2,033 for 90% power when using 100% of the observed effect. For planning at 75% of that effect, the figures are 2,645 and 3,540 per arm; at 50%, they are 5,821 and 7,791 per arm. These are hypothetical planning targets under the stated assumptions, not evidence about the probability that the completed trial detected an effect. 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 = 0.838; treatment proportion p₁ = 0.799; average p̄ = 0.819.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5450 = 1.0683.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5443 = 0.4581.
4. n = (1.0683 + 0.4581)² / (-0.0392)² = 1,518.9, rounded up to 1,519 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 <- 0.838120104438642                          # control proportion
p1 <- 0.798955613577023                          # 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(2275780)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,519 (80% power), 2,033 (90% power)
 75% of observed effect: n per arm = 2,645 (80% power), 3,540 (90% power)
 50% of observed effect: n per arm = 5,821 (80% power), 7,791 (90% power)
power.prop.test: 1518.9 
Simulated power at n = 1,519 per arm: 0.799 (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 analysis gives a treatment difference of 3.913 and a 95% confidence interval from -1.590 to 9.415, and the registry labels the analysis as non-inferiority. No p-value is listed for that analysis. Its treatment-difference direction and scale differ from the simple recalculation, which expresses the contrast as comparator minus doravirine and reports a risk difference of -0.039 with a 95% confidence interval from -0.094 to 0.015.

The arm-level percentages support the direction of the contrast: the reported Week 48 response percentage is higher for doravirine than for darunavir plus ritonavir. The sponsor’s reported treatment difference is on a percentage scale, whereas the simple recalculation is expressed on a proportion scale. Because these are not identical presentations or necessarily identical procedures, numerical values should not be compared without accounting for scale and contrast direction.

The registry record does not flag a discrepancy between the sponsor result and the recalculation. The recalculation is still a simple unadjusted analysis from posted summaries, not a replacement for the sponsor’s analysis. For the formal non-inferiority conclusion, the sponsor’s own analysis takes precedence. However, the non-inferiority margin and a clear statement of whether the criterion was met are not reported in the registry record, so the listed estimate alone is insufficient to confirm that conclusion independently.

15. Multiplicity, Missing Data and Analysis Populations

The registry summary identifies a primary non-inferiority question and says superiority would be assessed if non-inferiority were established. This is a testing sequence in principle, but the operational details are not reported in the registry record. In particular, the non-inferiority margin, the exact statistical procedure, and the decision rules governing any subsequent superiority assessment are not reported. Without those details, the formal inferential claim cannot be reconstructed from the posted percentages alone.

The registry lists multiple secondary outcomes and posts results for several related virologic endpoints. Testing many outcomes can increase the chance of false-positive findings when each result is interpreted separately. In general, a multiplicity plan may allocate error across outcomes, define a hierarchy, or otherwise control the overall chance of a misleading positive result. Whether such an approach was used is not reported in the registry record. The secondary recalculations are therefore described as unadjusted and should be treated cautiously.

For the primary endpoint, the registry states that all missing data were counted as treatment failures under the FDA snapshot approach, regardless of reason. This provides a clear rule but does not reveal the amount or pattern of missingness. The registry does not report sensitivity analyses using alternative assumptions for missing outcomes, so the robustness of the result to other missing-data approaches cannot be assessed from the available record.

The stated primary population comprises all randomized participants who received at least 1 dose of study drug. The registry does not report enough information to assess other analysis populations or how participants who did not meet that description were handled in every analysis. It also does not report detailed protocol deviations, the original sample-size justification, or a complete statistical analysis plan. These are reporting limitations: they do not show that a particular method was or was not used, only that the relevant information is not reported in the registry record.

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: appendicitis (0.5%), post procedural infection (0.5%), tuberculosis (0.5%), femur fracture (0.5%), post procedural haemorrhage (0.5%).

The registry reports serious adverse events affecting 45 participants in the doravirine group and 49 in the darunavir-plus-ritonavir group, with 383 listed at risk in each group. Deaths are reported as 3 in each group. The other adverse-event figures are 264 and 247, respectively, with 383 listed at risk in each group. These counts describe the posted safety record and should be read separately from the efficacy endpoint.

The listed serious-event terms with reported percentages are appendicitis, post procedural infection, tuberculosis, femur fracture, post procedural haemorrhage, and back pain, each at 0.5%. These entries are not a complete description of every safety event, and the registry information does not establish the cause of each event or whether an event was related to study treatment. The comparator safety group label includes a transition to doravirine, so it should not be treated as a simple description of uninterrupted comparator exposure throughout all follow-up.

Counts alone do not convey event timing, duration, severity beyond the serious-event classification, or individual clinical context. The posted safety figures are descriptive and do not establish that the regimens have identical or different safety profiles. The registry record does not report additional detail needed for a broader causal assessment.

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

The primary result describes a Week 48 comparison of the proportion meeting the HIV-1 RNA <50 copies/mL threshold. The posted percentages are 83.8% for doravirine and 79.9% for darunavir plus ritonavir. The recalculated unadjusted risk difference is -0.039 when written as comparator minus doravirine, with a 95% confidence interval from -0.094 to 0.015. That interval includes zero, so the simple difference analysis does not provide a precise separation from no difference under its usual interpretation.

The trial’s stated formal question was non-inferiority, not simply whether the percentages differed. A non-inferiority conclusion depends on comparing the result with a prespecified margin. That margin is not reported in the registry record. Although the sponsor analysis is labeled non-inferiority and reports a treatment difference of 3.913 with a 95% confidence interval from -1.590 to 9.415, the information reported does not state the margin or a clear conclusion. The formal criterion therefore cannot be independently confirmed from these figures alone.

The secondary virologic results have a broadly similar descriptive direction, but they are unadjusted and involve related outcomes at other thresholds or follow-up times. They do not replace the primary analysis, and the registry does not report whether multiplicity was controlled. Secondary findings should therefore be interpreted with less certainty than a result supported by a complete prespecified testing plan.

These results do not establish that one regimen is appropriate for an individual participant, nor do they summarize every potential benefit or harm. The reported safety counts are descriptive and do not establish causation. The endpoint is a group-level response measure under a specific missing-data rule, and the available confidence intervals express statistical uncertainty rather than all sources of uncertainty.

In general, a trial result is most informative when its population, endpoint definition, analysis method, missing-data handling, and decision threshold are considered together. Here, the record describes the primary population and missing-data rule, but does not report the non-inferiority margin, complete statistical plan, or sensitivity analyses. The posted data support a careful description of the observed outcomes; they do not by themselves answer every clinical or formal statistical question.

18. Why This Trial Matters Statistically

This trial illustrates why the label of an analysis matters. A randomized active-comparator trial can be designed to ask whether a new regimen is not unacceptably worse, rather than whether it is superior. The registry explicitly describes a non-inferiority hypothesis followed by a possible superiority assessment. The two questions require different decision criteria, so an ordinary unadjusted test of a difference cannot stand in for the planned non-inferiority evaluation.

It also illustrates the importance of the contrast scale and direction. The posted arm percentages favor doravirine numerically, while the recalculated risk difference is negative because it is expressed as comparator minus doravirine. A sign has meaning only alongside the stated subtraction order. Similarly, the sponsor’s treatment difference is reported on a different scale and direction. These distinctions matter when readers compare numbers across analyses.

The confidence intervals show why point estimates should not be read alone. The recalculated primary interval includes zero and spans a range of possible contrasts. The sponsor-reported interval also includes zero. Neither interval can resolve the non-inferiority question without the margin. A registry entry that gives an estimate but omits the decision margin leaves a key part of the inferential framework unavailable to readers.

Finally, missing-data rules and multiplicity affect interpretation. The snapshot approach counts all missing primary outcomes as failures, while the registry does not report the extent of missingness or alternative sensitivity analyses. Several secondary outcomes are reported without a stated multiplicity procedure. These features show why statistical interpretation requires more than comparing percentages: analysis population, endpoint handling, planned hypotheses, and uncertainty all shape what can be concluded.

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.

Several trial-specific reporting gaps limit interpretation. The registry record does not report the non-inferiority margin, although non-inferiority is the stated primary hypothesis. It also does not provide a clear formal statement that the criterion was met or the full decision rules for the planned sequence that could assess superiority afterward. The sponsor-reported estimate and interval therefore cannot be fully interpreted against the trial’s intended decision threshold.

The detailed statistical method for the sponsor analysis is not reported, and the primary sponsor result has no p-value listed. The recalculated comparison is an unadjusted calculation from posted summaries; it should not be assumed to reproduce the sponsor’s procedure. The registry also does not report the original sample-size justification or the design assumptions used for the completed trial. The planning illustrations based on the observed effect are not a substitute for those original assumptions.

Although missing values were treated as failures for the primary endpoint, the amount and pattern of missing data are not reported. Alternative missing-data analyses and sensitivity analyses are not reported in the registry record. The record also does not report a multiplicity adjustment or a full secondary-outcome testing hierarchy, making isolated secondary results less conclusive.

The primary population is described as randomized participants who received at least 1 dose of study drug. The registry does not provide enough detail to assess other analysis populations or all exclusions. Safety counts are available, but the event information reported does not establish causality or provide a complete account of timing and exposure. The comparator safety label indicates a transition to doravirine, which complicates interpretation of the safety counts as a simple comparison of exposure over the full study period.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy of Doravirine (MK-1439) in Participants With Human Immunodeficiency Virus 1 (HIV-1) (MK-1439-018) — NCT02275780.
• Registry record last updated 2024-10-01; status last verified 2024-09.
• Results first posted 2018-10-23.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT02275780 is a completed Phase 3 randomized, double-blind, parallel-group, active-comparator trial in treatment-naïve participants with HIV-1. It compared doravirine 100 mg once daily with darunavir 800 mg plus ritonavir 100 mg once daily, each combined with an investigator-selected TRUVADA™ or EPZICOM™/KIVEXA™ backbone. Registry enrollment is 769.

The primary endpoint was the percentage achieving plasma HIV-1 RNA <50 copies/mL at Week 48. The posted percentages were 83.8 for doravirine and 79.9 for the comparator. The simple unadjusted recalculation gives a risk difference of -0.039 for comparator minus doravirine, with a 95% confidence interval from -0.094 to 0.015. The registry identifies non-inferiority as the primary question, but the margin is not reported in the registry record.

The record describes an FDA snapshot approach that treats all missing primary endpoint data as failures. It also reports secondary virologic outcomes and safety counts. Missing statistical-plan details, including the non-inferiority margin and multiplicity handling, limit independent assessment of the formal conclusions.