Study to Evaluate the Efficacy, Safety and Tolerability of Vibegron in Men With Overactive Bladder (OAB) Symptoms on Pharmacological Therapy for Benign Prostatic Hyperplasia (BPH): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate the Efficacy, Safety and Tolerability of Vibegron in Men With Overactive Bladder (OAB) Symptoms on Pharmacological Therapy for Benign Prostatic Hyperplasia (BPH) (NCT03902080), a randomized phase 3 study. The primary outcome is Change From Baseline at Week 12 in the Average Number of Micturition Episodes Per Day.

2. Clinical Question

The primary outcome is a continuous measure: the average number of times per day that a participant voided in the toilet, recorded in a bladder diary. The registry defines change as the post-baseline value minus the baseline value, so a negative change represents a decrease in the daily average. The comparison is between randomized groups, not a comparison of each participant’s result with a fixed threshold.

This question is specific to men with overactive bladder symptoms while receiving pharmacological therapy for benign prostatic hyperplasia. It does not directly address other populations, other treatment regimens, or outcomes outside those recorded. The record also lists secondary questions about nocturia, urge urinary incontinence for participants with urinary incontinence at baseline, storage symptoms, and volume voided per micturition. Results are not posted for every listed secondary outcome.

3. Trial Design

The registry identifies this as a phase 3, randomized, double-blind, placebo-controlled, multicenter, parallel-group study. Masking is recorded as triple. Participants were assigned to vibegron 75 mg once daily or matching placebo once daily, with both treatment descriptions specifying 24 weeks. The registry lists an enrollment of 1105.

The study is titled as an evaluation of vibegron in men with overactive bladder symptoms who were receiving pharmacological therapy for benign prostatic hyperplasia. Its stated purpose was to assess efficacy compared with placebo using micturition and urgency episodes, alongside safety and tolerability. The primary analysis reported in the record concerns the change from baseline to Week 12 in average micturition episodes per day.

The record gives a start date of 2019-03-26 and a primary completion date of 2023-06-15, and lists the study status as completed. It identifies Urovant Sciences GmbH as sponsor. These registry entries describe the study’s broad design and timing; they do not establish all operational or analytic details.

The primary outcome results use the Full Analysis Set and include participants with data available at the specified time points. The numbers in the outcome analysis therefore need not match the total enrollment. The record does not report the original sample-size justification, detailed eligibility criteria, the full randomization procedure, or the precise contents of the masking arrangements. It also does not report the full statistical analysis plan, including all model specifications or any planned interim analyses.

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: Participants were enrolled in 82 sites across 8 countries. One randomized participant enrolled in the placebo group did not receive double-blind medication.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set. Only those participants with data available at specified time points have been presented.

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: Full Analysis Set consists of all randomized participants who took at least 1 dose of double-blind study treatment and had at least 1 evaluable change from Baseline mictruition

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline at Week 12 in the Average Number of Micturition Episodes Per Day, measured over Baseline; Week 12.

The primary endpoint is change from baseline at Week 12 in the average number of micturition episodes per day, measured as micturitions per day. A micturition was defined as a void in the toilet recorded in the bladder diary. Baseline was the last non-missing result on or before randomization. Change was calculated by subtracting the baseline value from the post-baseline value, and daily averages used event counts from complete diary days divided by the number of complete diary days.

This endpoint represents a repeated daily symptom measure rather than a single event. Expressing it as an average per day makes the groups’ changes interpretable on a common scale even when diary information comes from complete diary days. The outcome is continuous, so the reported group summaries are least-squares means and their standard errors.

The endpoint is used to compare average change between randomized groups at the specified follow-up time. A negative change indicates fewer recorded daily micturitions relative to baseline; the between-group estimate describes the difference in average change, not the change experienced by every participant. The record does not provide a threshold for a clinically important difference, so the statistical estimate alone cannot establish how meaningful a change would be to an individual participant.

7. Results Posted in the Registry

• Vibegron 75 Milligrams (mg) Once Daily (QD): mean -2.04 versus -1.30 on control; difference -0.74 (95% CI -1.04 to -0.44), standardized effect d = -0.30; z-test p = <0.001.

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.

Change From Baseline at Week 12 in the International Prostate Symptom Score (IPSS) Storage Score (1-week Recall)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Vibegron 75 Milligrams (mg) Once Daily (QD): mean -3.00 versus -2.20 on control; difference -0.80 (95% CI -1.16 to -0.44), standardized effect d = -0.28; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Vibegron 75 Milligrams (mg) Once Daily (QD) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline at Week 12 in the Average Volume Voided Per Micturition

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Vibegron 75 Milligrams (mg) Once Daily (QD): mean 25.63 versus 10.56 on control; difference 15.07 (95% CI 8.61 to 21.53), standardized effect d = 0.29; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Vibegron 75 Milligrams (mg) Once Daily (QD) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes covering nocturia, urge urinary incontinence among participants with urinary incontinence at baseline, the International Prostate Symptom Score storage score, and volume voided per micturition. Quantitative results are posted for the storage score and volume voided outcome, while results for nocturia and urge urinary incontinence are not reported in the registry record.

For the two posted secondary outcomes, the estimated changes favor a greater reduction in the storage score and a greater increase in volume voided per micturition in the vibegron group than in the placebo group. The sponsor’s analyses for these outcomes report p < 0.001. Their directions are broadly consistent with the primary result’s pattern of group differences, but secondary endpoints address distinct aspects of symptoms and voiding. They should not be treated as interchangeable measures or as confirmation of every possible effect.

Unadjusted secondary results carry less weight when several outcomes are examined because each additional test creates more opportunity for a statistically notable result to occur by chance. Whether and how the trial controlled the overall false-positive risk across outcomes is not reported in the registry record. The displayed secondary p-values should therefore be read as results for their individual comparisons, not as proof that the full set of secondary findings meets a prespecified multiplicity-adjusted standard.

The absence of posted results for some listed secondary outcomes also limits the overall picture. Their status as listed outcomes does not reveal the direction, size, or precision of their results. The available secondary findings can add context to the primary comparison, but they do not resolve the missing multiplicity and reporting details.

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

• Change From Baseline at Week 12 in the Average Number of Nocturia Episodes Per Night
• Change From Baseline at Week 12 in the Average Number of Urge Urinary Incontinence (UUI) Episodes Per Day for Participants With Urinary Incontinence at Baseline
• Change From Baseline at Week 12 in the International Prostate Symptom Score (IPSS) Storage Score (1-week Recall)
• Change From Baseline at Week 12 in the Average Volume Voided Per Micturition

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, and the registry reports least-squares means with standard errors. A least-squares mean is a model-based estimate of a group average. The registry identifies the sponsor’s method as Mixed Models Analysis, but the detailed model specification—including covariates, repeated-measures structure, and how the model handled incomplete observations—is not reported in the registry record. It is therefore not possible to reconstruct every feature of the sponsor’s analysis from the brief method label alone.

What does a mean difference represent?

A mean difference expresses the contrast between the groups’ average changes on the endpoint’s original scale. For the primary endpoint, that scale is micturitions per day. Its sign is interpreted in light of the change definition: change is the post-baseline value minus baseline, so a negative value represents a decrease. The reported difference compares the estimated average changes in the randomized groups. It does not describe the spread of individual participant outcomes or imply that all participants had the same response.

What does a standard error represent?

A standard error describes the sampling uncertainty in an estimated mean. It is not the standard deviation of individual outcomes. A smaller standard error generally corresponds to a more precise estimate, while a larger one indicates more uncertainty. The registry lists standard errors for the arm-level least-squares means. It does not report standard deviations for the primary outcome in the posted results, so individual-level variability cannot be read directly from those standard errors.

Why use a mixed model?

In general, mixed models can represent related observations from the same participant and can estimate group differences across outcome assessments while accounting for correlations among repeated measurements. That general description does not establish which repeated-measures structure or assumptions this trial used. The registry’s method label is not enough to determine the exact model or the assumptions applied to missing observations. Those details are not reported in the registry record.

How should the recalculation be understood?

The recalculated comparison uses posted summary statistics to make a simple, unadjusted estimate of the mean difference and its uncertainty. It is useful as a consistency check, but it does not reproduce a mixed model when the model’s specifications and participant-level data are unavailable. The recalculated p-value is also unadjusted. It should not be treated as an alternative sponsor analysis or as evidence that the model’s assumptions have been verified.

The registry’s reported primary analysis gives a mean difference of -0.74, a 95% confidence interval from -1.02 to -0.46, and p < 0.001. The unadjusted recalculation gives the same displayed mean difference and p <0.001. The registry indicates no discrepancy. The sponsor’s analysis is the primary source for the trial’s reported inference; the recalculation is supplementary and based on less information.

What does a p-value tell the reader?

In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test’s assumptions held. It is not the probability that the null hypothesis is correct, and it does not measure the size or importance of an effect. The reported p-value is associated with the sponsor’s analysis of the primary comparison. The registry does not report enough detail to assess the full testing strategy or any adjustment for multiple outcomes.

The analysis population matters alongside the method. The registry identifies the Full Analysis Set and says that only participants with data available at the specified time points are presented. It does not report a complete accounting of missing outcome observations or the method used to address them. Statistical interpretation should therefore distinguish the reported model-based estimate from what cannot be assessed about model assumptions, missingness, or multiplicity.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is -0.74 micturitions per day, with a 95% confidence interval from -1.02 to -0.46. The interval is entirely below zero, which is consistent with a greater average decrease in the vibegron group under the stated change definition. Its endpoints describe the range of values reasonably compatible with the model and data under the confidence-interval procedure; they are not a range containing 95% of individual participant changes.

Confidence intervals communicate both direction and precision. A narrower interval indicates less uncertainty about the estimated group contrast than a wider interval on the same scale. The interval gives a more informative view of the estimated difference than the p-value alone, because it shows the scale of contrasts compatible with the analysis. It still does not determine clinical importance: the registry record does not state a threshold for a clinically meaningful change.

The unadjusted recalculation also reports uncertainty around a mean difference of -0.74. Its interval is not identical to the sponsor’s reported interval, reflecting that a simple recalculation from summary statistics does not necessarily reproduce the mixed models analysis. The registry does not flag a discrepancy, and the sponsor’s reported analysis is the appropriate primary result to describe. A confidence interval cannot address unreported model assumptions, missing-data mechanisms, or the impact of testing multiple outcomes.

For the arm-level estimates, standard errors are reported as 0.109 in each group. These quantify uncertainty in the estimated means, rather than variation among individual observations. Precision should be read in context: the analysis counts are 503.0 and 507.0, while the trial enrollment is 1105, and the registry notes that only participants with data at the specified time points are presented.

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, not total events. They are illustrations based on the observed effect and are not the trial’s original design justification; that justification is not reported in the registry record. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

For the primary endpoint, planning for 100% of the observed effect gives 172 participants per arm for 80% power and 231 participants per arm for 90% power. Planning for 75% of the observed effect gives 306 participants per arm for 80% power and 410 participants per arm for 90% power. Planning for 50% of the observed effect gives 688 participants per arm for 80% power and 922 participants per arm for 90% power.

In plain terms, the 80% power column gives the per-arm planning count for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect is the true one and the assumptions hold. The 90% column gives the corresponding count for a higher planned chance of detection. A smaller target effect requires more participants per arm because it is harder to distinguish from random variation.

These are planning illustrations, not observed power. They do not establish what power the completed trial had under its actual design or analysis. The registry record does not report the trial’s original sample-size assumptions or justification.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.740; pooled standard deviation σ = 2.449.
2. n = 2 × (1.96 + 0.842)² × 2.449² / -0.740² = 172.0, rounded up to 172 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
delta <- -0.74                      # observed difference in means
sigma <- 2.44948959860025                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3902080)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 172 (80% power), 231 (90% power)
 75% of observed effect: n per arm = 306 (80% power), 410 (90% power)
 50% of observed effect: n per arm = 688 (80% power), 922 (90% power)
power.t.test: 173 
Simulated power at n = 172 per arm: 0.798 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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’s reported primary analysis is a Mixed Models Analysis. It gives a least-squares mean difference of -0.74, a 95% confidence interval from -1.02 to -0.46, and p < 0.001. This is the main reported inferential result for the primary endpoint.

The simple recalculation from the posted arm summaries also gives a mean difference of -0.74, with p <0.001. The recalculation is unadjusted and cannot reproduce all features of the mixed models analysis. Its confidence interval is not identical to the sponsor’s reported interval, so the two should not be presented as if they were the same analysis.

The registry marks the discrepancy flag as false. The sponsor’s reported analysis therefore does not conflict with the recalculation as recorded, and the sponsor’s model-based result remains the appropriate basis for describing the trial’s primary analysis. The recalculation is best understood as a transparent summary-statistic check, not as a competing trial result.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when statistical tests are conducted for several outcomes or comparisons. Even when each individual test uses a conventional significance threshold, considering many tests together increases the chance that at least one result appears statistically notable by chance. Adjustment procedures or a prespecified hierarchy can address this issue, but the registry record does not report whether either was used for the primary and secondary outcomes.

The primary outcome has a reported mixed models analysis, while secondary analyses are posted for selected outcomes. The record lists four secondary outcomes, but quantitative results are not reported for all of them. It does not state a testing hierarchy, a family of outcomes for multiplicity control, or adjusted p-values. Consequently, the displayed secondary p-values should be interpreted as individual results, and the status of any trial-wide error control is unknown.

For missing data, the registry identifies the Full Analysis Set and states that only participants with data available at the specified time points are presented. It does not report the number of missing primary outcome values, reasons for missingness, imputation rules, or sensitivity analyses. A mixed model can use available observations under particular assumptions, but the record does not give enough detail to determine the assumptions or handling used in this trial. No conclusion about the effect of missing data can be drawn from the available description alone.

The registry also does not report the trial’s original sample-size justification or interim-analysis plan. The planning illustrations based on the observed effect are not evidence of the original design assumptions. Taken together, these omissions constrain assessment of how the trial planned its statistical testing, handled unavailable outcomes, or protected against selective interpretation. They do not erase the reported estimates, but they are relevant to how confidently the full set of analyses can be interpreted.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: acute myocardial infarction (0.4%), head injury (0.4%), covid-19 pneumonia (0.2%), postoperative wound complication (0.2%), syncope (0.2%).

The registry reports serious adverse events among 24 of 553 participants at risk in the vibegron group and 16 of 551 participants at risk in the placebo group. It reports other adverse events affecting 79 of 553 participants at risk in the vibegron group and 71 of 551 participants at risk in the placebo group. The registry records 0 deaths in each group.

These are counts of participants affected, with the corresponding at-risk group sizes stated by the registry. They are not the primary efficacy outcome, and the at-risk counts differ from the primary outcome analysis counts. The record lists terms including acute myocardial infarction and head injury among its top serious adverse-event terms, but the posted summary does not provide enough detail to assess event timing, individual causality, or comparative risk beyond the listed counts.

Adverse-event counts are descriptive. Without additional information about definitions, follow-up, event adjudication, and statistical comparisons, they should not be interpreted as establishing that one group was safer or less safe overall.

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

The primary result describes a difference in average change in daily micturition episodes at Week 12 between randomized groups. The sponsor’s estimate is -0.74 micturitions per day, with a 95% confidence interval from -1.02 to -0.46 and p < 0.001. Under the endpoint definition, the negative estimate indicates a greater average decrease in the vibegron group than in the placebo group in the reported analysis.

This is a group-level statistical finding for a specified measure and assessment time. It does not mean that every participant experienced a decrease, that all participants experienced the estimated group difference, or that an individual response can be predicted from the group average. The confidence interval expresses uncertainty about the mean contrast, not the range of likely individual outcomes.

The result does not by itself establish the importance of the difference to participants. The registry record does not report a threshold for a clinically meaningful change. Nor does the primary outcome alone answer every question about overactive bladder symptoms, safety, durability, or outcomes beyond the recorded assessment. The study’s title and population also limit direct interpretation to men with overactive bladder symptoms receiving pharmacological therapy for benign prostatic hyperplasia; applicability to other populations or treatment settings is not established by this comparison.

The analysis should be read alongside the record’s limitations. The available description does not specify the full model, how missing outcome data were handled, or whether multiplicity was controlled across outcomes. Some listed secondary outcomes have no posted results. These omissions do not change the numerical primary estimate, but they limit what can be concluded about the broader evidence and the robustness of the full set of analyses.

18. Why This Trial Matters Statistically

This trial illustrates why the estimated contrast, its confidence interval, and its analysis method should be read together. The primary mean difference gives the direction and scale of the group comparison; the confidence interval communicates precision; and the mixed models label identifies the sponsor’s reported approach. The p-value alone would not convey the size of the estimate or the range of values compatible with the analysis.

It also highlights the distinction between a registry’s total enrollment and the population contributing to a particular outcome analysis. The record lists enrollment of 1105, while the primary analysis presents outcome-specific group counts and states that only participants with data at the specified time points are included. Those figures answer different questions and should not be treated as interchangeable.

The recalculation provides a useful check on the posted summary statistics, while the sponsor’s reported model remains the main inferential analysis. Their relationship is important: a simple calculation may agree in its displayed point estimate without reproducing the model or its interval. Finally, the secondary outcomes and planning illustrations show why unadjusted findings and retrospective planning calculations require careful framing. They add context, but they do not replace the trial’s original design rationale, full analysis plan, or complete outcome reporting.

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.

The registry description leaves several trial-specific details unreported. It does not give the original sample-size justification, the full statistical analysis plan, detailed model specifications, or the handling and reasons for missing outcome data. These gaps make it difficult to evaluate the assumptions behind the reported model and to determine how sensitive the result might be to alternative analytic choices.

Only participants with data available at the specified time points are presented for the primary outcome. The record does not provide a complete missing-data accounting or sensitivity analysis. Outcome-specific counts therefore describe the analyzed data, but do not explain the difference between those counts and total enrollment.

The registry lists four secondary outcomes but posts quantitative analyses for only two of them. It also does not report whether multiplicity was controlled. The secondary findings should be interpreted as individual comparisons, with the possibility that their inferential strength differs from that of a prespecified primary endpoint.

The posted primary outcome concerns one diary-based measure at Week 12. The registry record does not provide a clinical-importance threshold, so statistical evidence cannot alone establish the practical importance of the estimated difference. The safety summary is also limited to adverse-event counts and listed terms; it does not supply details needed to assess event timing, adjudication, or causal attribution.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate the Efficacy, Safety and Tolerability of Vibegron in Men With Overactive Bladder (OAB) Symptoms on Pharmacological Therapy for Benign Prostatic Hyperplasia (BPH) — NCT03902080.
• Registry record last updated 2024-08-07; status last verified 2024-06.
• Results first posted 2024-08-07.
• 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

NCT03902080 is a completed phase 3 randomized, double-blind, placebo-controlled, multicenter, parallel-group study of vibegron in men with overactive bladder symptoms receiving pharmacological therapy for benign prostatic hyperplasia. Participants were assigned to vibegron 75 mg once daily or matching placebo for 24 weeks, and enrollment was 1105.

The primary endpoint was change from baseline at Week 12 in average micturition episodes per day. The sponsor reported a least-squares mean difference of -0.74, with a 95% confidence interval from -1.02 to -0.46 and p < 0.001. The record also includes selected secondary analyses and adverse-event counts. Details about the original sample-size justification, multiplicity procedures, full model specification, and missing-data handling are not reported in the registry record.