Assess Safety and Efficacy of Vilaprisan in Subjects With Uterine Fibroids: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Assess Safety and Efficacy of Vilaprisan in Subjects With Uterine Fibroids (NCT03194646), a randomized phase 3 study. The primary outcome is Percentage Change in Bone Mineral Density (BMD) of Lumbar Spine.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, open-label, parallel-group, multicenter study comparing three vilaprisan schedules with standard of care in people with uterine fibroids. The registry lists an enrollment of 1272. That enrollment figure describes the overall trial record; it is not the number analyzed for the primary endpoint. The endpoint-specific groups include participants with measurements at the required time points, and the safety analysis set is defined separately in the registry.

The vilaprisan groups were A1, A2, and A3, each at 2 mg but with different treatment and bleeding-break schedules. The comparator, standard of care, was chosen by investigators and could be watch and wait or non-hormonal medical treatment. Since masking was listed as none, the study was open-label. The record does not report whether any particular outcome assessors were masked.

The study began on 2017-06-30, and primary completion was recorded as 2019-05-10. Its status is terminated. The reason for termination and any consequences for planned enrollment or follow-up are not reported in the registry record. The registry identifies Bayer as sponsor. It does not report the trial's original sample-size assumptions or enough detail to reconstruct the full protocol-level analysis plan.

Randomization supports comparison of assigned groups, but the primary endpoint analysis population was not simply everyone randomized: the stated safety set included vilaprisan participants who took at least one dose and all participants randomized to standard of care, with participants analyzed as treated. The primary endpoint description also restricts analysis to those with measurements at baseline and about one year after treatment started. These choices matter when interpreting the results, because the analysis summarizes observed endpoint data in the specified population rather than necessarily all randomized participants.

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: Overall, 2368 participants were screened. Of the 2368 screened participants, 1096 (46.3%) participants were not randomized to treatment due to screen failures. 1272 (53.7%) participants were randomized and 1238 (52.3%) participants received study treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Safety analysis set (SAF) was analyzed. SAF: All participants randomized to vilaprisan treatment groups who took at least 1 dose of study drug and all participants randomized to group B (standard of care) treatment group were included in the SAF. Participants were analyzed as treated. Overall number of participants analyzed represents number of participants without missing data.

5. Baseline Characteristics

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

Population: Participants in Full analysis set (FAS) was analyzed. The FAS consisted of all randomized subjects, excluding randomized subjects who did not start treatment Period 1 (never received study drug) due to the study being temporarily paused, including 1264 participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage Change in Bone Mineral Density (BMD) of Lumbar Spine, measured over From baseline to about 1 year after start of treatment.

The primary endpoint is percentage change in bone mineral density at the lumbar spine from baseline to about one year after treatment started. Bone mineral density was measured using dual-energy X-ray absorptiometry, or DEXA. The registry describes the endpoint as a mean with standard deviation, so the posted group summaries describe average change and the spread of individual values around that average.

Bone mineral density is a safety-related measure in this study: it tracks a skeletal measure during the treatment period. The registry also lists percentage change in bone mineral density at the hip and femoral neck among secondary outcomes, but the posted primary endpoint is specifically the lumbar spine. The endpoint analysis is limited to participants in the safety analysis set who had measurements at both stated time points.

A mean percentage change offers a concise group-level summary, but it does not show the full distribution of individual changes. Nor does it establish whether a particular change is clinically important: the registry record does not state a clinical threshold for interpreting the magnitude. It is also not a direct measure of uterine fibroid burden or bleeding symptoms. The endpoint should therefore be read as a comparison of average lumbar-spine bone-density change, within the specified analysis population and time frame.

7. Results Posted in the Registry

• Vilaprisan 2 mg A1 (3/1 Regimen): mean -1.56 versus 0.29 on control; difference -1.85 (95% CI -2.46 to -1.24), standardized effect d = -0.74; z-test p = <0.001.
• Vilaprisan 2 mg A2 (6/2 Regimen): mean -2.04 versus 0.29 on control; difference -2.33 (95% CI -2.86 to -1.80), standardized effect d = -0.96; z-test p = <0.001.
• Vilaprisan 2 mg A3 (3/2 Regimen): mean -1.51 versus 0.29 on control; difference -1.80 (95% CI -2.48 to -1.12), standardized effect d = -0.77; 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.

Number of Bleeding Days

• 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 deviations.
• Result:
  • Vilaprisan 2 mg A1 (3/1 Regimen): mean 1.57 versus 4.72 on control; difference -3.15 (95% CI -3.67 to -2.63), standardized effect d = -0.88; z-test p = <0.001.
  • Vilaprisan 2 mg A2 (6/2 Regimen): mean 1.74 versus 4.72 on control; difference -2.98 (95% CI -3.52 to -2.44), standardized effect d = -0.80; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Vilaprisan 2 mg A1 (3/1 Regimen) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Vilaprisan 2 mg A2 (6/2 Regimen) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists several kinds of secondary outcomes: bleeding days, endometrial histology findings, endometrial thickness, and bone mineral density at the lumbar spine and hip or femoral neck at time points other than the primary one. Among the secondary results described in the available endpoint information, bleeding days has posted group means and unadjusted recalculated comparisons. Numerical results for the other listed secondary outcomes are not reported in the registry record used for this analysis.

Bleeding days is related to the clinical context of uterine fibroids, whereas lumbar-spine bone mineral density is a distinct safety measure. These endpoints address different aspects of the study and should not be treated as interchangeable evidence. A pattern on one cannot fill in missing findings for the others. The bleeding-days comparison may add context to the primary endpoint, but it does not directly validate or explain the bone-density result.

Secondary outcomes typically carry less confirmatory weight when the analysis plan and multiplicity approach are not reported. Testing many outcomes can produce apparently notable results by chance, and selective reporting can complicate interpretation. The registry does not report a correction or hierarchy for secondary tests. Accordingly, unadjusted secondary comparisons are best read as exploratory signals rather than definitive evidence across the full set of outcomes. The registry's descriptions identify what was assessed, but the available numeric results do not allow a complete assessment of all those domains.

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

• Number of Bleeding Days
• Number of Participants With Endometrial Histology Findings by Endometrial Biopsy Main Results (Majority Read, Main Diagnosis)
• Change From Baseline in Endometrial Thickness
• Percentage Change From Baseline in BMD Measured at Lumbar Spine (Other Time Points Not Mentioned as Primary Safety Variable) and Hip/Femoral Neck

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a percentage change in bone mineral density. A group mean describes the average observed value, while a standard deviation describes how dispersed individual observations are around that mean. These answer different questions. A standard deviation is not a confidence interval and does not directly quantify how precisely the group mean or the difference between groups has been estimated.

What does a mean difference represent?

The mean difference compares the average endpoint value in a vilaprisan group with the average in standard of care. A negative estimate in this comparison means the vilaprisan mean is lower than the standard-of-care mean for percentage change. For example, the recalculated A1 estimate is -1.85. The quantity is expressed in the endpoint's percentage-change scale; it is not a relative percentage reduction between treatments. Each comparison is made against the same standard-of-care group, rather than being a direct comparison among the vilaprisan schedules.

The same reasoning applies to the secondary outcome of number of bleeding days, but its scale is days rather than percentage change. A mean difference of -3.15 for A1 means the observed average was lower in A1 than in standard of care by that estimated amount. It does not describe every participant's experience, and the group means do not reveal how the individual values overlap.

How should the p-values be read?

The recalculated p-values are unadjusted and are reported as < 0.001. In general, a p-value measures how incompatible the observed data are with a specified null hypothesis under the statistical model used. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. Because the registry record does not state a multiplicity procedure for these comparisons, the unadjusted p-values should not be treated as if they account for testing several groups or outcomes.

The registry does not report the method used for its own listed mean-difference analyses. The recalculations are simple unadjusted comparisons based on posted group means, standard deviations, and sample sizes. They do not incorporate covariates, stratification, repeated-measure modeling, or other adjustments unless those features are reflected in the posted summary statistics, which is not stated. These recalculations should therefore be distinguished from the sponsor's analysis.

Why does variability matter?

Comparisons depend both on the size of the difference in group means and on variability within groups. Greater variability generally makes a mean difference less precisely estimated when the group sizes stay the same. The pooled standard deviations used for the recalculated comparisons are 2.503 for A1, 2.423 for A2, and 2.341 for A3. These are summary measures used in the unadjusted calculations, not additional outcomes. The standard error describes the estimated sampling variability of a statistic; for example, the posted standard errors for the primary groups are 0.175 for standard of care, 0.257 for A1, 0.209 for A2, and 0.302 for A3. The registry does not report a model-based standard error for its own comparisons.

General statistical context: if data are more variable than a model assumes, standard errors and confidence intervals can be too small, making evidence appear more precise than it is. This concern is often discussed for count data with over-dispersion, where a simple Poisson model may understate variability. The primary endpoint is a continuous measure summarized by means and standard deviations, and the registry record does not report an over-dispersion model or a count model for it. The bleeding-days outcome is also summarized as a mean and standard deviation in the posted endpoint information; the record does not describe a distributional model for that outcome.

There are three vilaprisan-versus-standard-of-care primary comparisons, plus several listed outcomes. Testing multiple hypotheses can increase the chance of at least one small p-value if each is judged independently. A multiplicity adjustment changes the interpretation by controlling an error rate across a chosen family of tests. The registry record does not report whether such an adjustment was planned or used, nor does it identify a testing hierarchy. Consequently, the recalculated p-values should be understood as per-comparison, unadjusted results rather than as confirmatory evidence across all comparisons.

Randomization is intended to make assigned groups comparable on average, but analyses after randomization may differ from an intention-to-treat analysis if participants are excluded or grouped by treatment received. The registry says the safety set included vilaprisan participants who took at least one dose and all randomized standard-of-care participants, analyzed as treated. The primary endpoint additionally requires measurements at baseline and about one year after treatment started. The record does not explain how missing measurements were handled or whether the reported comparisons account for any departures from the randomized groups.

11. Confidence Intervals and Precision

A confidence interval gives a range of values compatible with the data and statistical assumptions used for the estimate. Its width reflects precision: narrower intervals indicate greater precision, while wider intervals indicate more uncertainty about the estimated mean difference. A confidence interval does not mean that a fixed proportion of individual participants had outcomes inside its limits.

The sponsor's posted 95% confidence intervals for the primary mean differences are -2.44 to -1.26 for A1, -2.87 to -1.80 for A2, and -2.51 to -1.10 for A3. Each interval lies below zero, so each is consistent with a lower mean percentage change in the vilaprisan group than in standard of care under the sponsor's analysis. The sponsor's point estimates are -1.85, -2.34, and -1.81, respectively.

The recalculated intervals are unadjusted and arise from summary-statistic calculations; their estimates and limits are close to the sponsor's reported results. The confidence limits from the recalculation are not a substitute for the sponsor's analysis. The standard-of-care and vilaprisan groups have different endpoint-analysis counts, and the A3 group is smaller than the other primary endpoint groups. In general, smaller groups tend to yield less precise estimates when other factors are similar, although interval width also depends on variability and the analysis method.

Precision is not the same as clinical importance. An interval can be narrow while the clinical meaning of its values remains uncertain if no meaningful-difference threshold is specified. The registry record does not report such a threshold for lumbar-spine bone mineral density. Nor do the intervals address uncertainty arising from missing outcomes, multiplicity, or departures from the analysis assumptions unless those issues were incorporated into the underlying model.

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 illustrative calculations based on the observed effect, not a reconstruction of the trial's original design. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row considers the full observed effect or a stated fraction of that effect. The registry record's original sample-size justification and design assumptions are not reported.

For these continuous outcomes, the planning figures are participants per arm, not total events. The distinction matters: a per-arm figure describes the planned size of each comparison group, whereas event totals are used for some time-to-event planning methods. The planning information explicitly notes that time-to-event tables use total events; that does not apply to these mean comparisons.

The 80% power column gives an illustrative per-arm sample size that, under the stated assumptions, would yield an 80% chance of detecting the chosen effect if that effect were the true one. The 90% power column uses a higher target probability of detecting that effect, so it generally calls for more participants per arm. These calculations concern a hypothetical future design; they do not describe what happened in the completed trial.

Planning for a smaller effect requires more participants, because a smaller difference is harder to distinguish from ordinary sampling variation. The rows using 75% or 50% of the observed effect illustrate that relationship. These are planning illustrations based on the observed results, not observed power. Observed power is not a useful retrospective measure of evidence: the estimated effect and its uncertainty are more informative for interpreting the study's results.

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 = -1.850; pooled standard deviation σ = 2.503.
2. n = 2 × (1.96 + 0.842)² × 2.503² / -1.850² = 28.7, rounded up to 29 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 <- -1.85                      # observed difference in means
sigma <- 2.50343434208981                     # 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(3194646)
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 = 29 (80% power), 39 (90% power)
 75% of observed effect: n per arm = 52 (80% power), 69 (90% power)
 50% of observed effect: n per arm = 115 (80% power), 154 (90% power)
power.t.test: 29.7 
Simulated power at n = 29 per arm: 0.788 (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 registry reports sponsor analyses of mean differences in final values, with 95% confidence intervals. For A1, the sponsor reports -1.85, with an interval from -2.44 to -1.26. For A2, it reports -2.34, with an interval from -2.87 to -1.80. For A3, it reports -1.81, with an interval from -2.51 to -1.10. The registry does not list p-values or the analysis method for those results.

The recalculated comparisons use the posted group means, standard deviations, and endpoint counts and are unadjusted. Their point estimates are close to the sponsor's estimates; small differences can arise because the sponsor's method is not described in the registry entry. The discrepancy flag is false. The sponsor's own analysis takes precedence as the trial's reported analysis, while the recalculations serve as a transparent statistical cross-check based on summary data.

The confidence intervals should also be interpreted as results of the sponsor's analysis rather than as intervals from the recalculation. Neither set of estimates establishes clinical importance without a stated threshold. Since the registry record does not identify the sponsor's model, covariate adjustments, or multiplicity procedure, the precise analytic basis of the sponsor results is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The record lists multiple vilaprisan schedules, the standard-of-care group, a primary endpoint, and several secondary outcomes. This creates multiple possible comparisons. When several hypotheses are tested, the chance of at least one false-positive result can increase if each is assessed independently. A prespecified multiplicity strategy can address that issue by defining which tests form a family and how the error rate is controlled.

The registry record does not report a multiplicity adjustment, testing hierarchy, or confirmatory status for the individual comparisons. The recalculated p-values are explicitly unadjusted. They should therefore be interpreted as results for each comparison rather than as an adjusted assessment across the full set of endpoints and groups. The registry's own reported analyses list confidence intervals but no p-values in the available record.

Missing-data handling is also not reported in the registry record. For the primary endpoint, the analysis is described for participants with measurements at baseline and about one year after treatment started. That requirement means the endpoint summary is based on observations at both time points; the record does not state how participants lacking either measurement were handled, whether values were imputed, or whether sensitivity analyses were conducted. The impact of missing measurements cannot be determined from the posted summaries alone.

The primary endpoint population is described as the safety analysis set. Vilaprisan participants had to be randomized to a vilaprisan group and take at least one dose; all participants randomized to standard of care were included; and participants were analyzed as treated. The endpoint description also specifies measured values at the two time points. This is not a complete description of an intention-to-treat analysis, and the registry does not report a separate intention-to-treat result. It does not report how protocol deviations, treatment discontinuation, or changes in treatment were handled in the primary analysis.

These omissions limit the ability to judge how robust the comparisons are to analysis choices. They do not demonstrate that the analyses were inadequate; they mean that the relevant procedures are not reported in the registry record.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hysterectomy (5.2%), uterine leiomyoma (2.8%), adrenal adenoma (2.3%), myomectomy (1.7%), heavy menstrual bleeding (1.4%).

The adverse-event listings separate treatment-emergent events from post-treatment events and report serious events, other events, and deaths for each group. In the treatment-emergent listings, serious events are reported for 15 of 349 in A1, 17 of 347 in A2, 6 of 177 in A3, and 17 of 365 in standard of care. The corresponding other-event counts are 136, 152, 56, and 90. Deaths are listed as 0 in each of these groups.

For post-treatment events, serious-event counts are 54 of 349 in A1, 42 of 347 in A2, 27 of 177 in A3, and 7 of 365 in standard of care; other-event counts are 75, 67, 44, and 14. Deaths are listed as 0 in each post-treatment group. These are registry counts with their listed denominators, not adjusted risk comparisons.

The serious-event terms shown most often include hysterectomy, uterine leiomyoma, adrenal adenoma, myomectomy, heavy menstrual bleeding, and adrenal mass. Adverse-event counts alone do not establish that treatment caused an event, and they do not describe severity, timing, or the clinical course for each participant. The record does not provide a comparative statistical analysis of these safety counts in the registry record for this explanation.

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

The posted primary results show lower mean lumbar-spine bone mineral density percentage change in each vilaprisan group than in the standard-of-care group over the stated time frame. The estimated differences are supported by confidence intervals that lie below zero in the sponsor's reported analyses, and the unadjusted recalculated p-values are < 0.001. These findings describe the measured endpoint in the analyzed participants; they do not establish what happened to every participant or what the change means clinically.

The results do not establish whether the observed bone-density differences are clinically important. The registry record does not report a threshold for a meaningful change, and the endpoint is not itself a measure of fibroid symptoms or fibroid size. Likewise, the bleeding-days summaries concern a separate outcome and cannot answer questions about endometrial histology, endometrial thickness, or other bone-density sites where numerical results are not reported in the registry record.

The study was open-label, and standard of care could differ according to investigator choice. The primary analysis population was defined by treatment received and available endpoint measurements, rather than being described as all randomized participants regardless of treatment or measurement availability. Missing-data methods and multiplicity procedures are not reported in the registry record. Those limits make the available summaries less complete than a full protocol and analysis report would be.

Safety listings add context but should not be read as causal evidence. Counts of serious and other events, even when reported with denominators, do not by themselves indicate whether an event was caused by study treatment or whether groups differed statistically. The record lists no deaths in the adverse-event group summaries, but this does not answer every question about safety or longer-term outcomes.

Overall, the record supports a bounded statement about average observed changes and posted event counts. It does not support broad claims about all benefits, harms, individual outcomes, or treatment choice.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definitions and analysis populations matter. The registry's overall enrollment is 1272, but the primary endpoint summaries use smaller endpoint-specific groups with measurements at both stated time points. Reading the overall enrollment as the denominator for every outcome would misrepresent what was analyzed. The definition of the safety analysis set also differs between vilaprisan and standard of care, so population details are essential to interpretation.

The record also separates a continuous safety measure from a symptom-related secondary outcome. Mean percentage change in bone mineral density and mean bleeding days use different scales and address different questions. Statistical significance in one endpoint cannot be transferred to another, and a group mean does not describe the full distribution of individual responses.

Comparison of sponsor results with summary-statistic recalculations offers a practical check on reported estimates, but it also demonstrates why the original method matters. The recalculations are unadjusted; the registry does not report the sponsor's method or a multiplicity plan. Reporting only summary numbers leaves uncertainty about covariate handling, missing data, and the broader family of tests.

Finally, planning calculations based on observed effects should not be confused with the trial's original design or with evidence that the study was adequately or inadequately powered. The original design assumptions are not reported, and retrospective observed power is not an informative substitute for effect estimates and confidence intervals. Clear reporting of these distinctions helps readers avoid treating a statistical result as a complete clinical conclusion.

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 record is marked terminated, but the reason for termination and its implications for recruitment, follow-up, or the planned analyses are not reported. The overall enrollment is listed, while the endpoint summaries use outcome-specific analysis counts. The record does not explain the movement from the overall enrollment to these particular endpoint populations, so completeness of follow-up cannot be assessed from the summaries alone.

The study was open-label. Standard of care was determined by investigators and could be watch and wait or non-hormonal medical treatment, meaning the comparator was not a single fixed intervention in the registry description. The record does not report whether outcome assessment was masked or whether the different forms of standard care were analyzed separately.

For the primary endpoint, the registry specifies a safety analysis set and requires measurements at baseline and about one year after treatment began. It does not report missing-data methods, sensitivity analyses, protocol-deviation handling, or a separate intention-to-treat analysis. The sponsor's analysis method and multiplicity approach are also not reported. The recalculations therefore provide only unadjusted comparisons based on summary statistics.

Although several secondary outcomes are listed, numerical results for most of them are not reported in the registry record used. The record also does not state a clinical threshold for interpreting bone-density change. Adverse-event counts are posted, but those counts alone do not establish causation or provide a full comparative safety analysis. These limitations restrict interpretation to the specific posted summaries rather than the full clinical and statistical evaluation of the trial.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Assess Safety and Efficacy of Vilaprisan in Subjects With Uterine Fibroids — NCT03194646.
• Registry record last updated 2025-07-28; status last verified 2025-07.
• Results first posted 2021-08-26.
• 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.

23. Record Summary

The registry describes NCT03194646 as a Phase 3, randomized, open-label, parallel-group, multicenter study of vilaprisan versus investigator-determined standard of care for uterine fibroids. Enrollment is listed as 1272, and the record status is terminated. Three vilaprisan 2 mg schedules were compared with standard of care.

The primary endpoint was mean percentage change in lumbar-spine bone mineral density from baseline to about one year after treatment started. The sponsor reported mean differences versus standard of care with 95% confidence intervals; unadjusted recalculations are close to those estimates. Bleeding days is a secondary outcome with posted group summaries and recalculated comparisons. Other listed secondary outcomes do not have numerical results reported in the registry record used for this analysis.

Adverse-event listings include treatment-emergent and post-treatment counts. Important analytic details, including the original sample-size assumptions, missing-data procedures, multiplicity strategy, and the sponsor's analysis method, are not reported in the registry record.