Effects of Switching From ATRIPLA™ (Efavirenz, Tenofovir, Emtricitabine) to MK-1439A (Doravirine, Tenofovir, Lamivudine) in Virologically-Suppressed Participants (MK-1439A-028): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effects of Switching From ATRIPLA™ (Efavirenz, Tenofovir, Emtricitabine) to MK-1439A (Doravirine, Tenofovir, Lamivudine) in Virologically-Suppressed Participants (MK-1439A-028) (NCT02652260), a randomized phase 2 study. The primary outcome is Percentage of Participants With at Least One Central Nervous System (CNS) Toxicity of at Least Grade 2 Intensity at Week 12.

2. Clinical Question

The clinical question is specifically about reported CNS symptoms of at least moderate intensity during the initial randomized comparison. It is not a general comparison of every effect of the regimens, nor does the primary endpoint measure viral suppression, overall quality of life or all adverse events. The study also collected other outcomes, including later CNS assessments, fasting lipids and HIV-1 RNA measures. Those outcomes address different questions and should not be treated as substitutes for the primary Week 12 comparison.

3. Trial Design

This was a Phase IIb, randomized, double-blinded, parallel-group study sponsored by Merck Sharp & Dohme LLC. The registry record lists HIV-1 and central nervous system conditions. Enrollment was 86. Participants were assigned to immediate or deferred switching, with 43 in each primary comparison arm.

Participants in the immediate-switch arm changed from ATRIPLA™ to blinded doravirine, tenofovir and lamivudine for the first 12 weeks, then continued with open-label treatment. Participants in the deferred-switch arm continued ATRIPLA™ for the first 12 weeks before switching to open-label treatment. This design allowed the primary outcome at Week 12 to compare switching with continued ATRIPLA™ while both groups were in the blinded portion of the study.

The registry lists a start date of 2016-03-04, primary completion on 2018-08-14, and completed status. The arm descriptions also include later open-label follow-up and extensions. Outcomes collected over these later periods have different timeframes from the primary randomized comparison; they should not be read as though they were all measured under the same treatment contrast.

The registry record does not report the method used to generate the randomization sequence, allocation concealment procedures, or the details of who was masked. It identifies the study as randomized and double-blinded. The original sample-size justification and the trial’s planned statistical assumptions are not reported in the registry record. The posted sample-size planning figures are illustrative calculations and are not the original design rationale.

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 112 participants screened, 86 were randomized and received study treatment.

Base Study

Reasons for not completing this period:

Study Extension 1 (Open-Label)

Reasons for not completing this period:

Study Extension 2 (Open-Label)

Reasons for not completing this period:

Study Extension 3 (Open-Label)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants who received at least one dose of study treatment, and have baseline data for analyses requiring baseline data.

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 With at Least One Central Nervous System (CNS) Toxicity of at Least Grade 2 Intensity at Week 12, measured over Week 12.

The primary endpoint is the percentage of participants with at least one CNS toxicity of Grade 2 or higher at Week 12. A questionnaire solicited ten symptoms: dizziness; depression or low mood; insomnia or sleeplessness; anxiety or nervousness; confusion; impaired concentration or attention; headache; somnolence or daytime sleepiness; aggressive mood or behavior; and abnormal dreams.

For each symptom, participants rated intensity from none (Grade 0) through mild (Grade 1), moderate (Grade 2) and severe (Grade 3). The registry describes mild symptoms as noticeable without interference with normal activities, moderate symptoms as having some impact on normal activities, and severe symptoms as preventing normal activities. The endpoint counts a participant if at least one of the listed symptoms reached Grade 2 or higher. It therefore summarizes whether a participant experienced a symptom at the specified intensity, rather than the number of symptoms or their combined severity.

This measure was used to address the trial’s stated question about CNS toxicity after switching from ATRIPLA™. A percentage is appropriate for an endpoint defined by the presence or absence of at least one qualifying symptom in each participant. The primary analysis used the last observation carried forward approach. The endpoint is a patient-reported symptom measure; it should not be interpreted as a direct measurement of a biological mechanism or as a complete measure of treatment tolerability.

7. Results Posted in the Registry

• Deferred Switch to MK-1439A: 37.2% (16/43) versus 41.9% (18/43) on control; risk difference -4.7 percentage points (95% CI -25.3 to 16.0), risk ratio 0.89 (0.53–1.50); unadjusted two-proportion z-test p = 0.659.

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 at Least One CNS Toxicity of at Least Grade 2 Intensity at Week 4

• 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:
  • Deferred Switch to MK-1439A: 65.1% (28/43) versus 46.5% (20/43) on control; risk difference 18.6 percentage points (95% CI -2.0 to 39.2), risk ratio 1.40 (0.95–2.06); unadjusted two-proportion z-test p = 0.082.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deferred Switch to MK-1439A and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With at Least One CNS Toxicity of at Least Grade 2 Intensity at Time of Switch, and at 24 Weeks Post-switch for the Combined Treatment Groups

• 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:
  • Combined Treatment Groups: Week 24 Post-Switch: 30.2% (26/86) versus 68.6% (59/86) on control; risk difference -38.4 percentage points (95% CI -52.2 to -24.6), risk ratio 0.44 (0.31–0.63); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Combined Treatment Groups: Week 24 Post-Switch than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With One or More Drug-related AEs Through Study Week 12

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Deferred Switch to MK-1439A: 20.9% (9/43) versus 32.6% (14/43) on control; risk difference -11.6 percentage points (95% CI -30.2 to 6.9), risk ratio 0.64 (0.31–1.32); unadjusted two-proportion z-test p = 0.223.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deferred Switch to MK-1439A and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the study’s focus beyond the primary Week 12 comparison. They include CNS symptom assessments at other timepoints, fasting lipid measures, later HIV-1 RNA outcomes, and adverse-event measures. Some assess change over time or combine treatment groups after switching, while others retain a comparison between the randomized groups. These differences in outcome definition and follow-up mean that the secondary results do not all estimate the same treatment contrast.

The overall pattern should be read as supporting context, not as a replacement for the primary endpoint. The primary result concerns the randomized comparison at Week 12; later combined-group assessments address follow-up after participants in both groups have switched. An observed change over time in a combined group cannot, by itself, isolate the effect of immediate versus deferred switching. Likewise, outcomes such as lipids or viral RNA address distinct domains from questionnaire-based CNS toxicity.

Secondary findings also have less interpretive weight when many outcomes or timepoints are examined without a reported multiplicity strategy. General statistical explanation: testing many hypotheses increases the opportunity for chance findings to appear noteworthy. Adjustment methods or a prespecified hierarchy can help control that risk, but the registry record does not report whether such a plan was used for the secondary outcomes. Unadjusted secondary results are therefore best treated as exploratory signals, interpreted alongside their definitions, timeframes and uncertainty, rather than as independent confirmation of the primary result.

The registry lists 19 posted secondary outcomes and 11 analyses. The existence of multiple outcomes does not establish that all were analyzed or reported under a single prespecified framework. A complete interpretation would require the planned analysis hierarchy, multiplicity adjustment details and information on missing observations, which are not reported in the registry record.

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

• Percentage of Participants With at Least One CNS Toxicity of at Least Grade 2 Intensity at Week 4
• Change From Baseline in CNS Toxicity Score at Week 4
• Change From Baseline in CNS Toxicity Score at Week 12
• Percentage of Participants With at Least One CNS Toxicity of at Least Grade 2 Intensity at Time of Switch, and at 24 Weeks Post-switch for the Combined Treatment Groups
• CNS Toxicity Scores at Time of Switch, and at 24 Weeks Post-switch for the Combined Treatment Groups
• Change From Baseline in Fasting Lipids at Week 12
• Change in Fasting Lipids Between Time of Switch and Week 24 Post-switch for the Combined Treatment Groups
• Percentage of Participants With HIV-1 RNA <50 and <40 Copies/ml at Week 24 Post-switch for the Combined Treatment Groups

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either did or did not have at least one qualifying CNS toxicity by Week 12. A percentage summarizes the frequency of that event in each arm. Comparing percentages preserves the clinical meaning of the endpoint: the contrast concerns the proportion of participants crossing the symptom threshold, not an average symptom score.

The recalculated contrast is a risk difference, expressed on the proportion scale. Its sign depends on the order of subtraction. The posted recalculation uses deferred switch minus immediate switch, so a negative value means the observed proportion was lower in the deferred-switch arm. A risk difference is an absolute contrast between proportions; it is not a relative change. Its confidence interval describes a range of values compatible with the data and the calculation method. When that interval includes zero, it includes no absolute difference as one possibility.

A p-value evaluates how unusual the observed data, or data more extreme, would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of a difference. The recalculated unadjusted p-value is 0.659. The sponsor-reported p-value is 0.331. These come from different analyses and should not be treated as interchangeable.

General statistical explanation: a confidence interval communicates uncertainty about an estimate, while a p-value summarizes evidence against a null value under a model. Neither one alone establishes clinical importance. A narrow interval would indicate greater precision; a broad interval leaves more plausible values unresolved. The registry’s reported primary interval and the recalculated interval are broad and span no difference.

The sponsor’s posted analysis identifies the Miettinen and Nurminen method and an estimated difference, with a 95% confidence interval. This method is used for comparing binomial proportions. The recalculation is an unadjusted calculation based on posted summary statistics. It is not a reconstruction of all elements of the sponsor’s analysis, such as any implementation details not stated in the registry record. The discrepancy indicator is false. No conflict is flagged between the sponsor result and the recalculation, but their estimates, interval limits and p-values are not identical. The sponsor-reported analysis remains the trial’s own reported analysis.

Relative measures can also describe a binary comparison. A risk ratio compares the event proportions as a ratio, while an odds ratio compares event odds. These measures answer different questions from a risk difference and may appear farther from or closer to the null value depending on the scale. The recalculated primary comparison includes a risk ratio of 0.889 with an interval from 0.526 to 1.501, and an odds ratio of 0.823 with an interval from 0.346 to 1.956. Both intervals include their respective null value of 1. General statistical explanation: for ratio measures, 1 represents equal event frequency on the ratio scale; for risk differences, 0 represents equal proportions.

The primary endpoint description specifies last observation carried forward (LOCF). In general, LOCF fills a missing later measurement with a participant’s last observed measurement. It can retain participants with incomplete follow-up, but it relies on an assumption that the carried-forward value is a reasonable substitute for the unobserved value. If symptoms change after the last assessment, that assumption may not hold. The registry does not report sensitivity analyses or enough detail to assess the effect of missing data on the primary estimate.

The planned sample-size illustrations use the observed effect and assume a two-sided significance level of 0.05, equal allocation between arms and a normal approximation. The calculations consider the full observed effect and smaller fractions of it. General statistical explanation: over-dispersion is a concern when outcome variation exceeds what a model assumes; it can make standard errors too small and intervals too narrow if ignored. The primary endpoint is binary, and the registry’s calculation description does not report an over-dispersion adjustment. More broadly, the original trial’s statistical plan, adjustment strategy and sample-size rationale are not reported in the registry record.

What does the arm comparison estimate?

It estimates the difference between the observed percentages meeting the symptom definition in the randomized arms at Week 12. This is a comparison of the assigned strategies during the initial period, not a comparison of all later follow-up as if treatment assignment remained unchanged.

Why keep the scales distinct?

An absolute difference, risk ratio and odds ratio express contrasts in different ways. They should not be mixed or described as though their numerical values have the same meaning. In particular, the sign of a difference depends on group order, while the null value for a ratio is 1.

11. Confidence Intervals and Precision

The primary recalculated risk difference is -0.046, with an interval from -0.253 to 0.160. Because the interval includes zero, the posted summary data are compatible with no difference as well as differences favoring either arm on the absolute-proportion scale. Its width indicates that the estimate does not pin down the size or direction of the contrast closely.

The sponsor-reported estimated difference is 4.65, with a 95% confidence interval from -15.92 to 24.85. That interval also spans zero. The sponsor analysis and the recalculation use different reported methods and presentation scales; their interval endpoints should be read within their own analyses, rather than combined. The recalculated risk-ratio interval, 0.526 to 1.501, and odds-ratio interval, 0.346 to 1.956, also include the ratio null value of 1.

General statistical explanation: a confidence interval reflects both the observed data and the assumptions of the method used to construct it. It is not a guarantee that the true effect lies within the interval, and it does not show which values are more likely without additional assumptions. A broad interval signals that the data leave substantial uncertainty about the effect size.

The primary arm percentages are based on 43 participants in each arm. With this enrollment, a modest difference in observed percentages can coexist with considerable uncertainty. The point estimate alone should not be read as a precise measure of the effect. The interval also does not establish equivalence: demonstrating equivalence would require a prespecified margin and an analysis designed for that purpose, neither of which is reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for the binary outcomes discussed in this comparison. They are not total events. The calculation description states a two-sided significance level of 0.05, equal allocation between the two arms and a normal approximation. It uses the observed effect as its starting point and illustrates planning for the full observed effect, 75% of the observed effect, and 50% of the observed effect. The trial’s original sample-size assumptions and justification are not reported in the registry record.

For the primary comparison, planning for 100% of the observed effect corresponds to 1,734 participants per arm for 80% power and 2,321 participants per arm for 90% power. Planning for 75% of the observed effect corresponds to 3,098 participants per arm for 80% power and 4,147 participants per arm for 90% power. Planning for 50% of the observed effect corresponds to 7,004 participants per arm for 80% power and 9,376 participants per arm for 90% power.

In general, 80% power means that a study designed under the stated assumptions would have an 80% chance of detecting the chosen effect at the specified significance level if that effect were the true one. The 90% column describes the corresponding design target with a higher chance of detection. Smaller effects require more participants because they are harder to distinguish from random variation. These figures are planning illustrations, not observed power. They do not describe what the completed trial was guaranteed to detect, and the original trial design assumptions are not reported in the registry record.

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 = 0.419; treatment proportion p₁ = 0.372; average p̄ = 0.395.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6914 = 1.3552.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6907 = 0.5813.
4. n = (1.3552 + 0.5813)² / (-0.0465)² = 1,733.4, rounded up to 1,734 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 <- 0.418604651162791                          # control proportion
p1 <- 0.372093023255814                          # 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(2652260)
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 = 1,734 (80% power), 2,321 (90% power)
 75% of observed effect: n per arm = 3,098 (80% power), 4,147 (90% power)
 50% of observed effect: n per arm = 7,004 (80% power), 9,376 (90% power)
power.prop.test: 1733.4 
Simulated power at n = 1,734 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 an estimated difference of 4.65, a 95% confidence interval from -15.92 to 24.85, and p = 0.331. The named method is Miettinen and Nurminen. The interval spans zero, so the reported estimate is uncertain about the direction and size of the difference.

The recalculation from posted summary statistics uses a risk difference of -0.046, with an interval from -0.253 to 0.160 and an unadjusted p-value of 0.659. Its subtraction order is deferred switch minus immediate switch. The sponsor’s estimate is reported separately, in a different presentation, and the two analyses should not be collapsed into a single number or treated as identical procedures.

The registry’s discrepancy indicator is false; no discrepancy is flagged. The sponsor’s analysis is the trial’s own reported analysis, while the recalculation is a simple unadjusted calculation from the posted arm summaries. The registry record does not report additional details that would explain every difference in estimate, interval or p-value. Both sets of results communicate substantial uncertainty, and neither provides a clear separation between strategies on the primary endpoint.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is clearly identified in the registry record, but the statistical plan for interpreting it alongside the secondary outcomes is not reported in the registry record. In particular, the record does not state whether a hierarchy of hypotheses, family-wise error control or another multiplicity procedure was prespecified. That matters because multiple outcomes, timepoints and comparisons can create more opportunities for chance findings. Without a reported plan, isolated secondary p-values should be interpreted cautiously and should not be treated as confirmatory evidence.

The primary analysis population is described as randomized participants who received at least one dose of study treatment and had baseline data for analyses requiring baseline data. This is not the same as an analysis of all randomized participants regardless of treatment exposure or baseline availability. The registry record does not describe the full handling of participants excluded from a particular analysis, the numbers with missing Week 12 data, or sensitivity analyses that might test how missing data affect the result.

The primary endpoint description says that last observation carried forward was used. General statistical explanation: this approach substitutes a participant’s last observed value for an unobserved later value. Its validity depends on whether that earlier value is a reasonable representation of the missing assessment. If symptoms change over time, carrying an earlier value forward can distort the estimated frequency. The direction and size of any such distortion cannot be determined from the reported information.

The registry record does not report whether interim analyses were conducted, whether stopping rules were used, or whether any adjustment for interim looks was planned. It also does not report the trial’s original sample-size justification or complete statistical analysis plan. These omissions limit assessment of whether the analyses and decision rules were established before outcomes were examined.

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: head injury (5.9%), breast cancer (5.9%), cystocele (5.9%), appendicitis (3.0%), wound sepsis (3.0%).

The serious adverse-event information is listed by treatment period. The immediate-switch group has 0 serious events at risk of assessment during Day 1 to Week 24; the deferred-switch group has 0 during Day 1 to Week 12. In the deferred-switch period from Week 12-36, 1 serious event is listed. The extension entries list 6 for immediate switch during Week 24-120, 2 for deferred switch during Week 36-132, 3 for immediate switch during Week 120-216, 1 for deferred switch during Week 132-228, 2 for immediate switch during Week 216-312, and 0 for deferred switch during Week 228-324. Deaths are listed as 0 in each period.

These are period-specific counts, not a direct estimate of comparative risk across a common follow-up duration. The periods have different lengths and differ in the treatment stage, so the counts should not be combined or compared as if exposure and observation were identical. Serious adverse events are also distinct from the broader category of other adverse events. The registry’s listed serious-event counts do not, on their own, establish causation or provide a complete account of tolerability.

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

The primary result describes the frequency of participants reporting at least one CNS symptom of moderate or severe intensity by Week 12. The observed percentages were 41.9% with immediate switching and 37.2% with deferred switching. The reported and recalculated comparisons have intervals that include no difference, and the recalculated estimate is not precise enough to settle the direction or size of a difference.

This does not establish that the strategies are equivalent. Equivalence requires a prespecified range of differences considered unimportant and an analysis designed to test that question; such a margin and plan are not reported in the registry record. Nor does the result prove that either strategy reduces or increases CNS symptoms. It is an estimate from a randomized study with limited enrollment and uncertainty around the comparison.

The endpoint is based on participant responses to a symptom questionnaire and a threshold of Grade 2 or higher. It does not capture every dimension of symptoms, such as duration, burden below the threshold, or the clinical meaning of each symptom for an individual. The last observation carried forward method adds assumptions when Week 12 information is missing.

The results should also be kept within their timeframe. At Week 12, the deferred-switch group was still continuing ATRIPLA™ while the immediate-switch group had changed treatment. Later follow-up includes open-label treatment and extensions, so it addresses different exposure conditions. Outcomes in those periods cannot be substituted for the initial randomized comparison.

In general, statistical uncertainty is not the same as proof that there is no effect. The posted data leave a range of plausible differences, including no difference. Clinical interpretation would also depend on the importance of the measured symptoms and the broader evidence, neither of which can be resolved by this endpoint alone.

18. Why This Trial Matters Statistically

This study illustrates why the choice of effect measure matters. The primary endpoint is a participant-level binary outcome, so an absolute difference in percentages directly describes how the observed event frequency contrasts between randomized arms. A relative measure such as a risk ratio or odds ratio answers a different question and should be interpreted on its own scale. The subtraction order also determines the sign of a risk difference, making the group order essential to interpretation.

It also shows why the estimate and its uncertainty must be read together. The primary percentages are not identical, but the comparison interval includes no difference and remains broad. A point estimate alone could overstate how firmly the data determine a treatment contrast. The sponsor analysis and the unadjusted recalculation provide separate statistical views of the posted results, rather than a reason to ignore uncertainty.

The clinical question is time-specific. Immediate versus deferred switching is a clear contrast during the first 12 weeks, but later follow-up involves open-label treatment and extensions. Keeping the timeframes distinct helps prevent a later within-group pattern from being mistaken for the original randomized comparison.

Finally, the record highlights the importance of methods transparency. The primary endpoint definition and LOCF approach are described, but the registry record does not report the complete statistical plan, missing-data sensitivity analyses, multiplicity strategy or original sample-size justification. Those details influence how confidently readers can interpret secondary findings and assess the robustness of the primary estimate. The sample-size illustrations also demonstrate that planning depends strongly on the effect a future study aims to detect; they are not a retrospective measure of the completed trial’s success.

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 primary comparison has 43 participants in each arm, and the confidence intervals are broad. The posted data therefore leave substantial uncertainty about the size and direction of the Week 12 contrast. The registry record does not report the original sample-size justification or the design assumptions used when the study was planned, which limits assessment of how the enrollment target related to the primary question.

The primary outcome is questionnaire-based and defined by whether at least one of ten symptoms reaches Grade 2 or higher. This thresholded measure does not show the full distribution of symptom severity, the number of symptoms per participant, or symptom duration. The registry record does not report validation details for the questionnaire or how responses were assessed if participants had incomplete symptom data.

The endpoint description specifies LOCF, but the record does not report the extent or pattern of missing Week 12 data, reasons for missingness, or sensitivity analyses using alternative assumptions. As a result, it is difficult to judge how much the primary estimate might depend on the missing-data approach.

The registry record also does not report the full statistical analysis plan, including multiplicity handling, interim analyses, or all prespecified analysis populations. The secondary outcomes span several domains and timeframes, and later treatment is open-label. These features make it important to avoid treating all follow-up results as a single randomized comparison or interpreting unadjusted secondary findings as definitive.

Finally, the serious adverse-event entries are divided into periods with differing durations and treatment stages. They are useful descriptive information, but they do not by themselves provide a standardized comparative safety estimate across the full study.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effects of Switching From ATRIPLA™ (Efavirenz, Tenofovir, Emtricitabine) to MK-1439A (Doravirine, Tenofovir, Lamivudine) in Virologically-Suppressed Participants (MK-1439A-028) — NCT02652260.
• Registry record last updated 2025-02-07; status last verified 2025-01.
• Results first posted 2019-08-29.
• 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

NCT02652260 is a completed randomized, double-blinded, parallel-group Phase IIb study sponsored by Merck Sharp & Dohme LLC. It enrolled 86 virologically suppressed participants with HIV-1 who were receiving ATRIPLA™ before screening. The primary comparison assessed CNS toxicities of Grade 2 or higher at Week 12 after immediate switching to doravirine, tenofovir and lamivudine versus continuing ATRIPLA™ before a deferred switch.

The posted Week 12 percentages were 41.9% for immediate switch and 37.2% for deferred switch. The sponsor-reported comparison and the unadjusted recalculation both leave substantial uncertainty about the difference. The registry record describes a questionnaire-based endpoint and LOCF, but does not report the complete statistical plan, multiplicity strategy, original sample-size rationale or sensitivity analyses for missing data. Secondary outcomes and later safety periods provide additional descriptive information but address distinct outcomes and treatment timeframes.