A Study to Assess Change in Disease Activity, Adverse Events, and How the Drug Moves Through the Body in Adult Participants Living With Human Immunodeficiency Virus (HIV) Receiving Intravenous (IV) Infusion or Subcutaneous (SC) Injection of Budigalimab and/or ABBV-382: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Assess Change in Disease Activity, Adverse Events, and How the Drug Moves Through the Body in Adult Participants Living With Human Immunodeficiency Virus (HIV) Receiving Intravenous (IV) Infusion or Subcutaneous (SC) Injection of Budigalimab and/or ABBV-382 (NCT06032546), a randomized phase 2 study. The primary outcome is Percentage of Participants With Viral Control Without Antiretroviral Therapy (ART) Restart.

2. Clinical Question

3. Trial Design

This was a Phase 2, randomized, double-blind, placebo-controlled, parallel-group study. The registry record describes quadruple masking and a multicenter design. Its official title states that it evaluated efficacy, safety, tolerability, and pharmacokinetics in people living with HIV who were on stable antiretroviral therapy and undergoing analytical treatment interruption. The study status is terminated.

The brief study description says that Part 1 used five treatment groups and Part 2 included an open-label arm for eligible participants. Part 1 compared different combinations of budigalimab, ABBV-382, and matching placebos. The arm descriptions specify intravenous doses on scheduled study days and weeks. The Part 2 description specifies open-label subcutaneous budigalimab. The brief description characterizes Part 1 as an eight-week dosing period and Part 2 as a six-week dosing period.

The primary outcome is reported at Week 24. The posted primary-outcome group sizes range from 20.0 to 42.0, and the ITT Population is specified for the endpoint. Recorded enrollment is 163. This figure describes enrollment for the study, not the number analyzed for every endpoint or group. The registry record does not report the number assessed for the primary endpoint or explain any differences between enrollment and endpoint group counts.

The registry record gives a study start date of 2023-10-12 and a primary completion date of 2025-09-22. These dates do not change the interpretation of the posted endpoint results; they provide the study’s recorded timing. The original design assumptions, allocation details beyond randomization, and reasons for termination 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT Population

5. Baseline Characteristics

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

Population: ITT Population

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Viral Control Without Antiretroviral Therapy (ART) Restart, measured over Week 24.

The primary endpoint is the percentage of participants in the ITT Population with viral control without restarting antiretroviral therapy at Week 24. Viral control is defined as viral load below 1000 copies/mL. The endpoint therefore combines a virologic threshold with a treatment-status condition at a specified follow-up time.

A percentage is useful for describing how often a defined outcome occurred in each assigned group. It makes the group results readable as proportions, while the accompanying confidence intervals convey uncertainty about those proportions. Here, the endpoint focuses on control during analytical treatment interruption rather than on a laboratory value measured while participants remain on antiretroviral therapy.

The endpoint does not capture every dimension of HIV disease activity or treatment experience. It does not, by itself, describe how long participants remained below the viral-load threshold, how quickly rebound occurred, or the reasons for restarting therapy. Those questions require other outcomes and definitions. The registry record lists median peak log10 viral load at rebound before restarting antiretroviral therapy and median time to first rebound to at least 1000 copies/mL during interruption as secondary outcomes.

Interpreting the percentage also depends on how participants with missing Week 24 assessments or other outcome-related events were handled. Those details are not reported in the registry record. The posted endpoint should therefore be read as the reported Week 24 proportion, with uncertainty reflected by its confidence interval, rather than as a complete account of each participant’s course.

7. Results Posted in the Registry

• Part 1: Budigalimab IV Mono: 10.0% (2/20) versus 5.0% (1/20) on control; risk difference 5.0 percentage points (95% CI -11.3 to 21.3), risk ratio 2.00 (0.20–20.33); unadjusted two-proportion z-test p = 0.548.
• Part 1: ABBV-382 IV Mono: 0.0% (0/20) versus 5.0% (1/20) on control; risk difference -5.0 percentage points (95% CI -14.6 to 4.6); unadjusted two-proportion z-test p = 0.311.
• Part 1: ABBV-1882 IV Low: 23.8% (10/42) versus 5.0% (1/20) on control; risk difference 18.8 percentage points (95% CI 2.8 to 34.8), risk ratio 4.76 (0.65–34.68); unadjusted two-proportion z-test p = 0.070.
• Part 1: ABBV-1882 IV High: 10.0% (4/40) versus 5.0% (1/20) on control; risk difference 5.0 percentage points (95% CI -8.3 to 18.3), risk ratio 2.00 (0.24–16.74); unadjusted two-proportion z-test p = 0.509.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either meets the stated Week 24 definition of viral control without restarting antiretroviral therapy or does not. The registry presents the result as a percentage in each group. A group percentage is an estimate, and it is more informative when read together with its confidence interval rather than as an exact population value.

What does a confidence interval express?

As a general statistical concept, a confidence interval describes uncertainty around an estimate under the analysis assumptions. A narrower interval indicates greater precision; a wider interval indicates less precision. It does not mean that every value inside the interval is equally plausible, and it does not establish that a result is clinically important. For the primary endpoint, the registry reports 90% confidence intervals for the group percentages.

The posted comparisons express differences in response rates between each listed treatment group and placebo. A difference of zero would represent equal estimated rates. An interval that includes zero is compatible with no difference under the interval’s method, as well as with values on either side of zero. An interval entirely on one side of zero indicates that the interval excludes zero, but interpretation still depends on the analysis plan, multiplicity, and the reliability of the data.

Why can small groups produce uncertain estimates?

As a general statistical concept, a proportion based on a small group can change noticeably when only a few participant outcomes differ. That makes the estimate sensitive to individual outcomes and commonly results in wider intervals. The posted group sizes for this endpoint are limited, and some response counts are very small. This is one reason not to interpret a single percentage as a stable estimate of an underlying rate.

The registry’s reported comparisons use the Mantel-Haenszel method and identify the parameter as response-rate difference. The record does not provide enough detail to reconstruct every aspect of that analysis, including any stratification factors or handling of missing outcomes. The sponsor’s listed comparisons include 90% confidence intervals and p-values. They are the sponsor’s analysis results and are distinct from unadjusted recalculations based on posted summary statistics.

What is the role of a p-value?

As a general statistical concept, a p-value measures how incompatible the observed data are with a specified null hypothesis under the analysis assumptions. It does not measure the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. A p-value should be interpreted with the estimated difference, its confidence interval, the endpoint definition, and the study design. Multiple comparisons can also make isolated p-values harder to interpret, particularly if the analysis does not account for the number of comparisons.

The primary outcome is identified as an ITT Population analysis. In general, an intention-to-treat approach aims to analyze participants according to their randomized assignment, preserving the comparison created by randomization. The label alone does not explain exactly how the registry analysis treated missing Week 24 data, treatment interruption, protocol deviations, or participants who restarted antiretroviral therapy. Those operational details are not reported in the registry record.

The study is described as randomized, parallel-group, double-blind, placebo-controlled, and quadruple-masked. Randomization can reduce systematic differences between assigned groups on average, while masking can reduce some forms of behavior or assessment influenced by knowledge of assignment. These are general design principles; the registry record does not provide enough detail to assess how randomization was implemented, which roles were masked, or whether masking was maintained.

Why does over-dispersion matter in some analyses?

As a general concept, over-dispersion occurs when observed variability is greater than a model assumes. It can lead to uncertainty estimates that are too small if the model does not account for that extra variability. The primary endpoint is a binary proportion, and the registry’s posted methods do not report an over-dispersion model. This concept may be relevant to other kinds of outcomes, but there is no basis in the registry record to claim that over-dispersion was assessed for this endpoint.

The secondary outcomes include median peak log10 viral load at rebound before restarting antiretroviral therapy and median time to first rebound to at least 1000 copies/mL during antiretroviral treatment interruption. They address different aspects of rebound than the Week 24 percentage. The registry record lists two posted secondary outcomes, but detailed results and analysis methods for those outcomes are not included in the registry record for this account.

10. Confidence Intervals and Precision

Precision is best judged from the confidence intervals, not from the point estimates alone. The 90% confidence intervals around the primary-outcome percentages are wide in several groups. Placebo is reported at 5.0%, with an interval from 0.26% to 21.61%. Part 1 ABBV-382 IV monotherapy is reported at 0.0%, with an interval from 0.0% to 13.91%. Part 1 ABBV-1882 IV Low is reported at 23.8%, with an interval from 13.53% to 37.03%. These intervals show substantial uncertainty around the underlying proportions.

The intervals for group differences also matter. For the sponsor-reported comparison of ABBV-1882 IV Low with placebo, the response-rate difference is 18.8, and the 90% confidence interval runs from 5.35 to 32.27. For budigalimab IV monotherapy, the reported difference is 5.0, with an interval from -8.64 to 18.64. Intervals spanning zero leave considerable uncertainty about the direction of the difference; even an interval not spanning zero does not remove uncertainty about its size or practical importance.

Precision is limited by the posted group sizes and the number of observed outcomes, especially where few participants met the endpoint. A zero observed percentage does not prove that the underlying rate is zero; the reported interval for ABBV-382 IV monotherapy extends above zero. Likewise, a higher point estimate does not, on its own, establish that a group’s underlying rate is reliably higher than placebo.

Confidence intervals are not substitutes for details about the analysis population and missing data. The registry record does not report the handling of missing Week 24 measurements or the original precision targets. The result is therefore most accurately described as a set of group estimates with notable uncertainty, rather than as a precise ranking of the treatment groups.

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 illustrations give the number of participants per arm for 80% power and the number of participants per arm for 90% power for selected two-group comparisons. These are per-arm participant counts, not total participants across both arms and not total event counts. The sample-size assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The original trial’s own design assumptions are not reported in the registry record.

For example, planning for 100% of the observed ABBV-1882 IV Low effect gives 54 participants per arm for 80% power and 72 participants per arm for 90% power. Planning for 75% of that observed effect gives 83 participants per arm for 80% power and 110 participants per arm for 90% power. Planning for 50% gives 155 participants per arm for 80% power and 207 participants per arm for 90% power. The different rows illustrate how the planning requirement changes when the target effect is smaller.

In plain language, 80% power means that, under the stated planning assumptions and if the target effect were the true effect, the design would have an 80% chance of detecting it using the specified test criterion. The 90% power column describes the corresponding chance under that higher target power. Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions.

These figures are planning illustrations based on observed effects, not the original study’s sample-size justification. They are not observed power: they do not describe the probability that the completed study’s result is true or the probability that a treatment effect exists. They also should not be treated as recommendations for a future study without considering its own endpoint, assumptions, analysis plan, and population.

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 = 0.050; treatment proportion p₁ = 0.100; average p̄ = 0.075.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3725 = 0.7301.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3708 = 0.3121.
4. n = (0.7301 + 0.3121)² / (0.0500)² = 434.4, rounded up to 435 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 <- 0.05                          # control proportion
p1 <- 0.1                          # 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(6032546)
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 = 435 (80% power), 582 (90% power)
 75% of observed effect: n per arm = 714 (80% power), 955 (90% power)
 50% of observed effect: n per arm = 1,471 (80% power), 1,969 (90% power)
power.prop.test: 434.4 
Simulated power at n = 435 per arm: 0.807 (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. Analyses Reported by the Sponsor

The sponsor’s reported primary-outcome comparisons use the Mantel-Haenszel method and provide response-rate differences with 90% confidence intervals and p-values. For budigalimab IV monotherapy versus placebo, the sponsor reports a difference of 5.0, with a 90% confidence interval from -8.64 to 18.64. For ABBV-382 IV monotherapy, the difference is -5.0, with an interval from -13.02 to 3.02. For ABBV-1882 IV Low, it is 18.8, with an interval from 5.35 to 32.27. For ABBV-1882 IV High, it is 5.0, with an interval from -6.19 to 16.19.

Simple recalculations from the posted summary statistics are also available for several comparisons. The discrepancy flag indicates that those recalculations do not fully agree with the sponsor’s analysis. The sponsor’s own analysis takes precedence for describing the formal registry results; recalculated estimates are unadjusted checks, not a substitute for the sponsor’s method or analysis.

The posted recalculations do not include a corresponding sponsor-reported comparison for Part 2 budigalimab SC monotherapy. Nor does the registry record explain the source of the discrepancies or provide sufficient detail to resolve them. The reported methods and results should therefore be kept distinct rather than combining recalculated and sponsor estimates as if they were one analysis.

14. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is clearly identified, but the registry record does not report how the study handled multiplicity across treatment comparisons or outcomes. Several groups are compared with placebo, and the record lists secondary outcomes as well. When many hypotheses are assessed, the chance of at least one apparently unusual result can increase. As a general statistical principle, prespecified multiplicity procedures can address that issue; whether such procedures were used in this study is not reported in the registry record.

The sponsor’s primary-outcome comparisons are labeled superiority analyses. The registry record does not provide a complete statistical analysis plan, a hierarchy of testing, or a description of whether the comparisons were confirmatory or exploratory. The reported p-values should therefore be read as results of the listed analyses, not as evidence that any unreported multiplicity strategy was applied.

The primary outcome specifies the ITT Population, but the registry record does not explain how missing Week 24 viral-load data were handled, whether participants with incomplete follow-up were included in the denominator, or what assumptions were made for unavailable outcomes. It also does not report sensitivity analyses for missing data or explain the treatment of protocol deviations. These details matter because a percentage can change depending on how missing outcomes are classified or excluded.

The registry record does not report whether interim analyses were planned or conducted, whether stopping boundaries were used, or whether the sample size was based on a prespecified power calculation. The planning illustrations based on observed effects do not establish the trial’s original design rationale. The reason the study was terminated is also not reported in the registry record.

These absences do not invalidate the posted numbers, but they limit how fully the statistical claims can be assessed. Interpretation should rely on the stated endpoint, the listed sponsor analysis, the reported uncertainty, and the explicit limits of the available analysis details.

15. 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 (10.0%), pyelonephritis acute (5.3%), hernia pain (5.0%), cellulitis (5.0%), glioblastoma (5.0%).

The serious adverse event figures report the number at risk and the number affected in each listed group. The registry lists 0 serious adverse events among 21 at risk for Part 1 placebo; 5 among 20 for Part 1 budigalimab IV monotherapy; 1 among 19 for Part 1 ABBV-382 IV monotherapy; 8 among 42 for Part 1 ABBV-1882 IV Low; 8 among 40 for Part 1 ABBV-1882 IV High; and 0 among 21 for Part 2 budigalimab SC monotherapy. The listed death count is 0 in every group.

These are descriptive counts, not proof that the underlying risks are equal or different. The groups have limited numbers at risk, so the observed counts alone provide little precision about uncommon events. The registry record also lists serious-event terms and percentages, including appendicitis at 10.0%, acute pyelonephritis at 5.3%, hernia pain at 5.0%, cellulitis at 5.0%, glioblastoma at 5.0%, and retroviral rebound syndrome at 4.8%. The record does not assign those terms to a particular group in the available information.

Serious adverse events are distinct from other adverse events. The posted counts do not establish causality or provide a complete benefit-risk assessment. The registry record does not report the detailed event definitions, follow-up exposure, or the sponsor’s interpretation of these safety findings.

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

The Week 24 results describe the percentage of participants in each listed group who met a specific definition: viral load below 1000 copies/mL without restarting antiretroviral therapy. The observed percentages range from 0.0% to 23.8%. The confidence intervals show that these estimates are uncertain, and the group sizes and numbers of responses are limited. The figures are therefore a snapshot of the posted endpoint, not a definitive ranking of the regimens.

The sponsor’s reported comparisons provide estimates and 90% confidence intervals for four Part 1 comparisons with placebo. The interval for ABBV-1882 IV Low does not include zero, while its reported p-value is 0.072. The other listed sponsor intervals include zero. These results require cautious interpretation, especially because the registry does not report how multiplicity was addressed and the sponsor analysis differs from simple unadjusted recalculations.

The endpoint does not say how long viral control lasted or whether participants later restarted antiretroviral therapy. It should not be interpreted as an outcome for every aspect of HIV disease, as a measure of long-term health, or as a complete account of rebound. The listed secondary outcomes address rebound timing and peak viral load, but their results are not included in the information available for this analysis.

The adverse-event counts describe events recorded in the listed groups. They do not establish that a drug caused an event, and the small group counts limit conclusions about uncommon harms. A zero count in a group does not establish that the risk is absent. The registry record is marked terminated, but the reason is not reported; no causal link between termination and the results can be inferred from that status alone.

Overall, the posted evidence describes observed proportions and serious adverse event counts with substantial uncertainty and incomplete analysis detail. It does not support a broad conclusion about treatment effectiveness, long-term outcomes, or comparative safety beyond the specific reported measures.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate should not be read in isolation. A group with a higher observed viral-control percentage may also have a wide confidence interval, and the interval may overlap values compatible with a smaller difference. Reporting uncertainty alongside each percentage makes the limitations of small groups visible.

It also highlights that the choice of endpoint shapes the question being answered. Viral control without antiretroviral therapy restart at Week 24 is a specific combined outcome, not a general measure of disease status or durability. The secondary outcomes listed in the registry address other aspects of rebound, which are conceptually distinct from the primary percentage.

The discrepancy between the sponsor’s analysis and simple recalculations is another important statistical lesson. Recalculation from summary data can serve as a check, but it may not reproduce the sponsor’s method. The sponsor’s analysis takes precedence for the formal reported comparisons, while the difference underscores the value of clear methods and transparent analysis details.

Finally, planning illustrations derived from observed effects are not evidence of the study’s original design assumptions and are not observed power. Their usefulness lies in showing how the required planning size changes when the target effect changes under stated assumptions. The registry record does not report its original sample-size rationale, multiplicity strategy, missing-data procedures, or reason for termination, all of which would help place the reported results in a fuller statistical context.

18. 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 limits affect interpretation. The primary endpoint is a Week 24 percentage, and the registry record does not describe how missing endpoint data were handled or provide sensitivity analyses. The record identifies the ITT Population but does not give additional details needed to assess the analysis denominator and treatment of participants without a Week 24 assessment.

The posted group sizes are limited, and some observed response counts are small. This makes group percentages imprecise and leaves the results sensitive to a small number of outcomes. The sponsor reports comparisons for four Part 1 groups versus placebo, but the registry record does not report a multiplicity procedure. A sponsor comparison for Part 2 budigalimab SC monotherapy is not listed.

The registry describes ABBV-382 in the study title and intervention list, but some primary-outcome group labels say ABBV-1882. The record does not explain the naming discrepancy. This makes it important to retain the posted labels when describing the endpoint groups rather than assuming that the names are interchangeable.

The registry record is marked terminated, with the reason not reported. It does not provide the original sample-size justification, a complete statistical analysis plan, details of interim analyses, or the basis for the termination status. The available information also does not include detailed results for the listed secondary outcomes. These gaps prevent a complete reconstruction of the planned and executed analyses.

The safety information is presented as group counts and selected serious-event terms. It does not provide enough detail to establish causality, compare event rates with precision, or assess exposure-adjusted risks. These limitations should be kept in mind when reading both efficacy and safety findings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study to Assess Change in Disease Activity, Adverse Events, and How the Drug Moves Through the Body in Adult Participants Living With Human Immunodeficiency Virus (HIV) Receiving Intravenous (IV) Infusion or Subcutaneous (SC) Injection of Budigalimab and/or ABBV-382 — NCT06032546.
• Registry record last updated 2026-11-06; status last verified 2026-11.
• Results first posted 2026-11-06.
• 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.

22. Record Summary

The registry record describes a randomized, double-blind, placebo-controlled, parallel-group Phase 2 study with quadruple masking in adults living with HIV on stable antiretroviral therapy and undergoing analytical treatment interruption. Recorded enrollment is 163; the study status is terminated. The primary endpoint is the percentage with viral control below 1000 copies/mL without antiretroviral therapy restart at Week 24 in the ITT Population.

Posted group percentages range from 0.0% to 23.8%, with 90% confidence intervals that reflect substantial uncertainty. The sponsor reports Mantel-Haenszel comparisons for four Part 1 groups versus placebo. Simple recalculations differ, and the sponsor’s analysis takes precedence. Serious adverse event counts and selected event terms are also listed; deaths are recorded as 0 in each group. The reason for termination, missing-data procedures, multiplicity approach, and original sample-size rationale are not reported in the registry record.