Dose Ranging, Switch Study of Islatravir (MK-8591) and Ulonivirine (MK-8507) Once-Weekly in Virologically-Suppressed Adults With Human Immunodeficiency Virus Type 1 (HIV-1) [MK-8591-013]: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dose Ranging, Switch Study of Islatravir (MK-8591) and Ulonivirine (MK-8507) Once-Weekly in Virologically-Suppressed Adults With Human Immunodeficiency Virus Type 1 (HIV-1) [MK-8591-013] (NCT04564547), a randomized phase 2 study. The primary outcome is Percentage of Participants Who Experienced One or More Adverse Events (AEs) During the Double-Blind Treatment Period +42 Days Post-Blind.

2. Clinical Question

The trial asks a descriptive safety question across three once-weekly dose combinations and an active-control regimen. Its primary endpoint counts participants with one or more adverse events, rather than the total number of events. An adverse event is defined in the registry record as an untoward medical occurrence temporally associated with study intervention, whether or not it was considered related to that intervention.

The record reports the percentage with at least one adverse event in each arm. It also gives recalculated, unadjusted risk-difference comparisons. These comparisons are not a substitute for a sponsor analysis; no sponsor analysis results are posted in the registry record. The key interpretive issue is the degree of uncertainty around the between-group estimates, not simply which reported percentage is numerically larger.

3. Trial Design

This was a randomized, active-controlled, double-blind, dose-ranging Phase 2 study; the official title describes it as Phase 2b. The registry lists triple masking and a parallel-group model. The record does not specify which roles were masked, how the randomization sequence was generated, or how allocation was concealed.

The study enrolled 161 participants. Four groups were described: once-weekly islatravir 20 mg plus ulonivirine 100 mg, 200 mg, or 400 mg, and once-daily BIC/FTC/TAF as the active control. Participants in the three combination groups received placebo to BIC/FTC/TAF; those in the control group received placebos corresponding to the two once-weekly study drugs. The registry identifies the primary endpoint population as all randomized participants who received at least one dose of double-blind study intervention.

The primary endpoint covered the double-blind treatment period and the 42 days following the final dose of double-blind study intervention, with a stated timeframe of up to approximately 9 months. Following study-wide discontinuation of study intervention, participants may have entered an optional, unblinded safety-monitoring period and received standard-of-care non-study antiretroviral therapy. The registry also reports safety groups for this later period; those figures should be distinguished from the primary endpoint period.

The study started on 2021-03-09, had primary completion on 2025-01-30, and is listed as completed. The reasons for selecting the enrollment target, original sample-size assumptions, details of the treatment period, and planned interim analyses are not reported in the registry record.

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: As pre-specified in protocol amendment 2, participants in the Double-blind Treatment Period discontinued all study interventions (islatravir \[ISL\], ulonivirine, or bictegravir/emtricitabine/tenofovir alafenamide \[BIC/FTC/TAF\]). Participants who received ISL + ulonivirine may have then entered the Unblinded Safety Monitoring Period and received standard of care non-study antiretroviral therapy (ART), provided by the investigator, until study completion or discontinuation.

Double-blind Treatment Period

Reasons for not completing this period:

Unblinded Safety Monitoring Period

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 double-blind study intervention

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 Who Experienced One or More Adverse Events (AEs) During the Double-Blind Treatment Period +42 Days Post-Blind, measured over Up to approximately 9 months.

The primary endpoint is the percentage of participants who experienced one or more adverse events during double-blind treatment plus 42 days after the final dose. It is a binary participant-level measure: a participant is counted as having an event if at least one adverse event occurred in the specified period. The endpoint does not express the number of separate events per participant, the severity of every event, or whether an event was judged related to treatment.

The registry defines an adverse event as an untoward medical occurrence temporally associated with study intervention, regardless of whether it was considered related. This broad definition supports a general safety and tolerability assessment during the study period. The registry describes this endpoint as prespecified in the protocol and supplemental statistical analysis plan, but further details of those documents are not reported in the registry record.

Percentages are reported for the four randomized groups. The denominators are 40, 41, 40, and 40 participants, respectively. The reported percentages were 75.0% for the 100 mg ulonivirine group, 75.6% for the 200 mg group, 80.0% for the 400 mg group, and 67.5% for BIC/FTC/TAF. These figures describe the proportion of participants with at least one event; they do not establish that an event was caused by a study drug. They also do not, by themselves, show how precisely the group percentages differ.

7. Results Posted in the Registry

• Group 2: ISL 20 mg + Ulonivirine 200 mg: 75.6% (31/41) versus 75.0% (30/40) on control; risk difference 0.6 percentage points (95% CI -18.2 to 19.4), risk ratio 1.01 (0.79–1.29); unadjusted two-proportion z-test p = 0.949.
• Group 3: ISL 20 mg + Ulonivirine 400 mg: 80.0% (32/40) versus 75.0% (30/40) on control; risk difference 5.0 percentage points (95% CI -13.3 to 23.3), risk ratio 1.07 (0.84–1.35); unadjusted two-proportion z-test p = 0.592.
• Group 4: BIC/FTC/TAF: 67.5% (27/40) versus 75.0% (30/40) on control; risk difference -7.5 percentage points (95% CI -27.3 to 12.3), risk ratio 0.90 (0.68–1.19); unadjusted two-proportion z-test p = 0.459.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary at the participant level: each person either experienced one or more adverse events during the specified period or did not. A percentage is a natural summary for this kind of outcome because it expresses how common the event was within each group. The group denominators matter: percentages based on relatively small groups can shift noticeably when only a few participants have a different outcome.

What does a risk difference express?

A risk difference subtracts the event proportion in one group from the event proportion in another, with the direction determined by the stated comparison. It is an absolute contrast, rather than a relative measure. The recalculated comparisons use the 100 mg ulonivirine group as the reference. For 200 mg, the risk difference was 0.006; for 400 mg, it was 0.05; and for BIC/FTC/TAF, it was -0.075. A positive value means the event proportion in the compared group is higher than in the reference group under this comparison convention; a negative value means it is lower. These are unadjusted estimates.

The registry also includes recalculated risk ratios and odds ratios. In general, a risk ratio compares the event probabilities directly, while an odds ratio compares the odds of an event. Both are relative measures and are interpreted differently from an absolute risk difference. When outcomes are common, risk ratios and odds ratios need not be numerically similar. The risk difference is often the more direct way to describe an absolute contrast, while the relative measures offer another scale for comparison.

How should p-values be read?

The reported p-values for the recalculated comparisons are 0.949, 0.592, and 0.459. A p-value describes how compatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. These p-values are unadjusted. The registry does not report sponsor-run comparison analyses or a multiplicity-adjusted testing procedure.

Because the outcome is binary, the comparison calculations rely on counts of participants with and without an adverse event in each group. The posted summaries include 30 events among 40 participants in the reference group. The compared groups include 31 among 41 for 200 mg, 32 among 40 for 400 mg, and 27 among 40 for BIC/FTC/TAF. These counts correspond to the arm percentages reported for the primary endpoint. The registry does not report any covariate adjustment for the recalculated comparisons.

What do confidence intervals add?

A confidence interval gives a range of estimates compatible with the data under a statistical procedure. It communicates uncertainty around an estimate that a single percentage, risk difference, or p-value cannot convey. Here, each recalculated risk-difference interval spans zero. That means the interval includes the no-difference value and also allows differences on either side of zero. The intervals are wide, so the data do not pin down the size or direction of the contrasts precisely. The registry record does not state the confidence level or give a sponsor analysis method for these intervals.

In general, confidence-interval width depends on factors including the number of participants, the event frequencies, and the method used. More observations often improve precision, though the exact result depends on the data and design. A confidence interval is not a guarantee that the true value lies within its endpoints, nor does it show the probability that a particular effect is true.

Why can event variability matter?

Over-dispersion is a general concern when observed outcomes vary more than a statistical model assumes. For a binary endpoint, the basic participant-level outcome is an event or no event, but clustering, repeated observations, or other departures from a model can affect uncertainty estimates when relevant to the design. The primary endpoint is described as one or more events per participant over a defined period, not as a count of all recurrent events. The registry does not report an over-dispersion adjustment, a repeated-event model, or evidence that such a method was used.

The registry labels the trial randomized, active-controlled, double-blind, and triple-masked, but does not report the detailed randomization or masking procedures. It also does not report whether analyses were stratified, which statistical test was prespecified for the primary endpoint, how missing outcomes were handled, or whether an intention-to-treat analysis was planned. The primary endpoint population is described as randomized participants who received at least one dose of double-blind study intervention. That description should not be expanded into unreported assumptions about other analysis populations.

The posted p-values and effect estimates are explicitly recalculated, simple, unadjusted summaries. In general, an adjusted model or a prespecified sponsor analysis may address design features or other variables differently, but the registry record does not provide such an analysis for these comparisons. The calculations should be treated as aids to understanding the posted counts, not as evidence of a complete inferential analysis plan.

10. Confidence Intervals and Precision

The arm percentages are 75.0%, 75.6%, 80.0%, and 67.5%, with denominators of 40, 41, 40, and 40, respectively. These point estimates describe the observed proportions, but do not convey their precision by themselves. With groups of this size, each estimate is based on a limited number of participants, so uncertainty around the underlying proportions and between-group contrasts is important.

The recalculated risk-difference confidence intervals are broad and each spans zero. For the 200 mg comparison, the reported interval extends from -0.182 to 0.194; for 400 mg, from -0.133 to 0.233; and for BIC/FTC/TAF, from -0.273 to 0.123. The intervals therefore include both no difference and effects in either direction. Their width indicates that the observed data do not estimate the risk differences tightly. The confidence level is not reported in the registry record.

Precision is distinct from whether a p-value falls below a chosen threshold. A broad interval can be compatible with a range of effects, and a single p-value cannot show that range. Conversely, an estimate near zero does not establish that the groups are equivalent. The registry does not report an equivalence or non-inferiority margin, and no such conclusion should be inferred from the posted comparisons.

These intervals accompany simple, unadjusted recalculations, not a posted sponsor analysis. Their interpretation also depends on the statistical method used; the detailed method and confidence level are not reported in the registry record. The arm percentages and event counts are useful descriptions of what was observed, while the intervals caution against treating small numerical differences as precise estimates.

11. 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 illustrative calculations based on the observed effect in each comparison, not the trial's original design assumptions. Each listed sample size is the number of participants per arm, not the total across both arms and not a total number of events. The registry record does not report the trial's original sample-size justification or design assumptions.

The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect: 100%, 75%, or 50%. The columns for 80% and 90% power describe the number of participants per arm that the illustration estimates would be needed to have an 80% or 90% chance of detecting the specified effect under those assumptions, if the assumptions and effect were correct. Power is a property of a planned study under an assumed effect; it is not the probability that the observed result is true.

For example, the 200 mg versus 100 mg comparison has planning estimates of 78,516 participants per arm for 80% power and 105,109 per arm for 90% power when using 100% of the observed effect. The corresponding estimates rise to 139,873 and 187,249 when planning for 75% of the observed effect, and to 315,363 and 422,181 for 50%. This illustrates the general pattern: smaller effects require more participants to detect with the same target power, other assumptions held fixed.

Results differ by comparison because the observed effect differs. The 400 mg and active-control comparisons have their own planning estimates, and those estimates should not be treated as evidence that the trial had adequate power for its original objectives. These are planning illustrations, not observed power; the trial's own design rationale is not reported in the registry record.

12. 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 = 0.750; treatment proportion p₁ = 0.756; average p̄ = 0.753.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6099 = 1.1953.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6098 = 0.5133.
4. n = (1.1953 + 0.5133)² / (0.0061)² = 78,515.1, rounded up to 78,516 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 <- 0.75                          # control proportion
p1 <- 0.75609756097561                          # 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(4564547)
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 = 78,516 (80% power), 105,109 (90% power)
 75% of observed effect: n per arm = 139,873 (80% power), 187,249 (90% power)
 50% of observed effect: n per arm = 315,363 (80% power), 422,181 (90% power)
power.prop.test: 78515.1 
Simulated power at n = 78,516 per arm: 0.808 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists three pairwise comparisons, each using the 100 mg ulonivirine group as the reference: 200 mg, 400 mg, and BIC/FTC/TAF. The associated p-values are described as unadjusted recalculations. No multiplicity correction, hierarchical testing procedure, or other approach to controlling the consequences of multiple comparisons is reported in the registry record. Looking at several comparisons can increase the chance of finding an apparently notable result by chance, so these p-values should not be treated as if they were adjusted confirmatory tests.

The registry reports zero sponsor analyses for the posted primary endpoint comparisons. It does not provide a detailed statistical analysis plan, the sponsor's inferential methods, or results from an adjusted analysis. The endpoint description says that the primary outcome was prespecified in the protocol and supplemental statistical analysis plan, but the relevant details are not reported in the registry record.

The stated primary endpoint population includes randomized participants who received at least one dose of double-blind study intervention. The record does not describe an intention-to-treat analysis population or provide additional details about the analysis set used for each comparison. It also does not report how participants with missing endpoint information were handled, whether missing outcomes occurred, or whether imputation or sensitivity analyses were used. Missingness therefore cannot be assumed to have been absent or inconsequential.

The record does not describe stratification factors, covariate adjustment, interim analyses, stopping rules, or a procedure for handling deviations from the assigned intervention. These details are not reported in the registry record and should not be inferred from the randomized, masked, parallel-group design. The limited posted information supports a descriptive reading of the arm percentages and the recalculated unadjusted comparisons, but does not establish how a complete prespecified analysis would address multiplicity or missing data.

14. 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: skin laceration (2.7%), device related thrombosis (2.5%), campylobacter gastroenteritis (2.5%), cellulitis (2.5%), kaposi's sarcoma (2.5%).

During the listed treatment groups, serious adverse events were reported for 2 of 40 participants in the 100 mg ulonivirine group, 3 of 41 in the 200 mg group, 1 of 40 in the 400 mg group, and 0 of 40 in the BIC/FTC/TAF group. The registry reports no deaths in any of these groups. These are counts of participants with serious adverse events, not the primary endpoint of any adverse event.

The record also lists other adverse events for 18, 15, 25, and 14 participants in those same groups, respectively. Serious and other adverse-event summaries should be kept distinct, and neither category by itself establishes that the intervention caused an event. The listed serious-event terms include Skin laceration at 2.7%, Device related thrombosis at 2.5%, Campylobacter gastroenteritis at 2.5%, Cellulitis at 2.5%, Kaposi's sarcoma at 2.5%, and Acute myocardial infarction at 2.4%.

Separate safety groups describe participants after study intervention was discontinued and non-study antiretroviral therapy was used. Those figures cover a different period and should not be combined with the double-blind treatment summaries. The registry record does not provide enough detail to infer causality or to draw conclusions about rare events from these counts.

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

The posted results describe the proportion of participants in each group who experienced at least one adverse event during the defined primary endpoint period. The observed percentages ranged from 67.5% in the BIC/FTC/TAF group to 80.0% in the 400 mg ulonivirine group. The 100 mg and 200 mg groups had reported percentages of 75.0% and 75.6%. These are descriptions of the study participants, not proof that any regimen caused or prevented events.

The recalculated unadjusted comparisons show little precision: each risk-difference confidence interval spans zero, and the reported p-values are 0.949, 0.592, and 0.459. The intervals also allow differences in either direction. Thus, the posted comparisons do not establish that the groups are the same, and they do not establish a reliable difference. The study enrolled 161 participants overall, with group denominators of 40, 41, 40, and 40 for the primary endpoint.

The endpoint includes any adverse event meeting the registry definition, whether or not considered related to study intervention. It is not a direct measure of drug-related harm, event severity, or the total number of events per person. Serious adverse-event counts are separately reported and are small in these groups; a lack of reported deaths does not rule out risk or establish safety for outcomes that may be uncommon.

The record does not report sponsor analysis results for the comparisons, a multiplicity adjustment, detailed missing-data handling, or the confidence level for the recalculated intervals. It also does not report the trial's original sample-size rationale. Consequently, the available results support cautious description of observed event frequencies and uncertainty, not a definitive ranking of regimens, proof of equivalence, or conclusions about effects beyond the participants and periods described.

16. Why This Trial Matters Statistically

This trial illustrates why an observed percentage should not be read in isolation. The primary endpoint percentages differ numerically across the groups, but their denominators are limited and the recalculated risk-difference intervals are broad. A point estimate gives the center of an estimate; an interval communicates how uncertain that estimate remains. Both are needed for a careful comparison.

It also highlights the distinction between a broad safety endpoint and a treatment-attributed outcome. The primary measure counts participants with at least one adverse event, regardless of whether the event was considered related to the intervention. Serious adverse events are reported separately. Neither measure alone identifies causation, and counts from a later safety-monitoring period represent a different timeframe from the primary endpoint.

Statistically, the three comparisons share a reference group, while the posted p-values are unadjusted. This makes multiplicity relevant to interpretation: several comparisons should not be treated as a single isolated test. The registry record does not report a multiplicity plan or sponsor-run analyses for these comparisons, so the recalculated results are best regarded as descriptive and exploratory rather than definitive evidence.

The planning illustrations reinforce a further point: the number of participants required depends strongly on the effect being targeted. A smaller effect generally requires a larger study to detect under the same assumptions. These calculations are not the original rationale for the trial and do not show the probability that the observed effects are real. Overall, the record is a useful example of reading event percentages alongside denominators, uncertainty, endpoint definitions, and analysis limitations.

17. 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 endpoint groups contain 40, 41, 40, and 40 participants, and the resulting estimates have limited precision. The recalculated confidence intervals for the risk differences are wide and include zero. Consequently, the point estimates do not tightly determine the size or direction of between-group contrasts.

The posted comparisons are unadjusted recalculations, and the registry reports no sponsor analysis results for them. It does not report a multiplicity adjustment despite listing three comparisons against the same reference group. The confidence level and detailed calculation method for the intervals are not stated in the registry record. Results should therefore be interpreted as descriptive statistical summaries, not as a complete account of the prespecified analysis.

Details of missing outcome data, imputation, sensitivity analyses, treatment adherence, and analysis populations beyond the primary endpoint population are not reported in the registry record. The randomization and masking procedures, including which roles were masked, are also not detailed. The original sample-size justification and any interim-analysis plan are not reported.

The endpoint captures at least one adverse event, whether or not judged related to study intervention. It does not distinguish causality in the primary summary, quantify recurrent events, or provide a complete characterization of event severity. Serious adverse-event counts are small, and the record does not support conclusions about uncommon outcomes. The optional post-discontinuation safety-monitoring period is distinct from the primary endpoint period; its figures should not be interpreted as if they were part of the double-blind treatment endpoint.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Dose Ranging, Switch Study of Islatravir (MK-8591) and Ulonivirine (MK-8507) Once-Weekly in Virologically-Suppressed Adults With Human Immunodeficiency Virus Type 1 (HIV-1) [MK-8591-013] — NCT04564547.
• Registry record last updated 2026-01-26; status last verified 2026-01.
• Results first posted 2026-01-26.
• 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.

21. Record Summary

NCT04564547 is a completed randomized, active-controlled, masked Phase 2 study of once-weekly islatravir 20 mg plus three ulonivirine dose levels, compared with once-daily BIC/FTC/TAF, in adults with virologically suppressed HIV-1. The study enrolled 161 participants. The primary endpoint was the percentage with one or more adverse events during double-blind treatment and 42 days after the final dose, up to approximately 9 months.

Reported endpoint percentages were 75.0%, 75.6%, 80.0%, and 67.5% across the 100 mg, 200 mg, 400 mg, and active-control groups. Recalculated unadjusted comparisons have broad confidence intervals spanning zero. The registry record does not report sponsor analysis results, multiplicity adjustment, detailed missing-data methods, or the original sample-size justification. The posted data support descriptive interpretation with substantial uncertainty.