A Study to Evaluate the Efficacy, Safety and Tolerability of Mirabegron and Solifenacin Succinate Alone and in Combination for the Treatment of Overactive Bladder: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy, Safety and Tolerability of Mirabegron and Solifenacin Succinate Alone and in Combination for the Treatment of Overactive Bladder (NCT01340027), a randomized phase 2 study. The primary outcome is Change From Baseline to End of Treatment (EOT) in Mean Volume Voided Per Micturition.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, factorial, parallel-group, active- and placebo-controlled, multicenter dose-ranging study. The registry lists Phase 2, randomized allocation, and triple masking. It was sponsored by Astellas Pharma Europe B.V. The record lists enrollment of 1307 and gives the study start as 2011-03-29 and primary completion as 2012-06-28; its status is completed.

The treatment arms included matching placebo, mirabegron 25 mg or 50 mg, solifenacin 2.5 mg, 5 mg, or 10 mg, and six combinations of solifenacin and mirabegron. Participants took tablets orally once a day for 12 weeks. The factorial structure allowed investigation of different dose combinations alongside monotherapy groups, but the registry record does not report the original planned contrasts or a complete analysis plan for interpreting the factorial effects.

The primary outcome was change from baseline to end of treatment in mean volume voided per micturition, with baseline and Week 12 specified as the timeframe. The registry reports arm-level least-squares means with standard errors and sponsor analyses using ANCOVA for primary-endpoint comparisons. The Full Analysis Set required at least one dose after randomization and diary-derived primary data at baseline and at least one post-baseline visit. The record describes last observation carried forward imputation, but its description is incomplete. Further details of the trial’s original sample-size justification and statistical plan are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: After screening, 1658 participants entered a 2-week, single-blind, placebo run-in period. After completion of the run-in period, 1307 participants were randomly assigned to 1 of the 12 treatment arms in a 1:1:1:1:2:1:2:2:2:2:1:1 ratio.

Only the first 6 of 12 groups are shown.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) comprised all participants took at least 1 dose of double-blind study medication after randomization and had primary efficacy data (mean volume voided) derived from the diary at Baseline and at least 1 post-baseline visit. Last observation carried forward imputation (LOCF) was utilized.

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: Baseline Measure data are provided for all randomized patients who took at least 1 dose of double-blind study drug (Safety Analysis Set). One participant randomized to the Mirabegron 25 mg arm received treatment with Solifenacin 5 mg + Mirabegron 50 mg in error and is counted in that arm for safety analysis set analyses.

Only the first 6 of 13 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline to End of Treatment (EOT) in Mean Volume Voided Per Micturition, measured over Baseline and Week 12.

The primary endpoint is the change from baseline to end of treatment in mean volume voided per micturition, measured in mL. For each participant, the mean was calculated from the volume of each micturition recorded in a diary for 3 days before the baseline and Week 12 clinic visits. The endpoint therefore summarizes the volume associated with an average urination over the diary period, rather than the total volume over a day.

A change score puts the Week 12 measure in relation to the participant’s baseline value. The reported arm estimates are least-squares means, which are model-based estimates; the registry reports standard errors as their measure of dispersion. In comparisons, a positive difference relative to placebo indicates a larger estimated increase in mean volume voided per micturition in the treatment group. That direction describes the measurement, not a clinical recommendation or a conclusion about overall benefit.

Diary-based measures can capture repeated everyday observations, while the use of a defined diary period gives a consistent basis for the clinic-visit summaries. The registry’s primary analysis population required usable baseline and post-baseline diary data. The full details of how the model handled the repeated diary measurements, beyond the information in the registry record, are not reported in the registry record.

7. Results Posted in the Registry

• Mirabegron 25 mg: mean 24.90 versus 14.00 on control; difference 10.90 (95% CI -5.69 to 27.49), standardized effect d = 0.21; z-test p = 0.198.
• Mirabegron 50 mg: mean 34.50 versus 14.00 on control; difference 20.50 (95% CI 3.97 to 37.03), standardized effect d = 0.39; z-test p = 0.015.
• Solifenacin 2.5 mg: mean 36.40 versus 14.00 on control; difference 22.40 (95% CI 5.87 to 38.93), standardized effect d = 0.42; z-test p = 0.008.
• Solifenacin 5 mg: mean 36.00 versus 14.00 on control; difference 22.00 (95% CI 7.65 to 36.35), standardized effect d = 0.42; z-test p = 0.003.

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 to End of Treatment in Mean Number of Micturitions Per 24 Hours

• 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:
  • Mirabegron 25 mg: mean -2.48 versus -2.43 on control; difference -0.05 (95% CI -0.87 to 0.77), standardized effect d = -0.02; z-test p = 0.904.
  • Mirabegron 50 mg: mean -2.56 versus -2.43 on control; difference -0.13 (95% CI -0.94 to 0.68), standardized effect d = -0.05; z-test p = 0.754.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Mirabegron 25 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Mirabegron 50 mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to End of Treatment in Mean Number of Incontinence Episodes Per 24 Hours

• 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:
  • Mirabegron 25 mg: mean -0.74 versus -0.95 on control; difference 0.21 (95% CI -0.87 to 1.29), standardized effect d = 0.14; z-test p = 0.704.
  • Mirabegron 50 mg: mean -0.90 versus -0.95 on control; difference 0.05 (95% CI -0.95 to 1.05), standardized effect d = 0.03; z-test p = 0.922.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Mirabegron 25 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Mirabegron 50 mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to End of Treatment in Patient Perception of Bladder Condition (PPBC)

• 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:
  • Mirabegron 25 mg: mean -1.40 versus -1.40 on control; difference 0.00 (95% CI -0.39 to 0.39), standardized effect d = 0.00; z-test p = 1.000.
  • Mirabegron 50 mg: mean -1.50 versus -1.40 on control; difference -0.10 (95% CI -0.49 to 0.29), standardized effect d = -0.08; z-test p = 0.614.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Mirabegron 25 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Mirabegron 50 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering micturition frequency, incontinence episodes, voided volume, response categories, and patient perception of bladder condition. These outcomes add different perspectives on bladder symptoms, but they are not substitutes for the primary diary measure of mean volume per micturition. The posted secondary means show that patterns vary by outcome and treatment group; a consistent conclusion across all secondary measures should not be assumed.

Some secondary endpoints have much smaller analysis groups than the primary endpoint, particularly the incontinence-episode outcome. Smaller groups generally lead to less precise estimates, and the uncertainty should be judged from the relevant endpoint’s own results rather than inferred from the primary analysis. The registry posts 29 secondary outcomes, while the full results are spread across numerous analyses. The breadth of outcomes increases the importance of knowing which comparisons were planned and how multiplicity was handled.

Unadjusted secondary results carry less weight as confirmatory evidence when many outcomes and treatment contrasts are examined. A nominal p-value does not account for the chance findings that can arise from repeated testing unless a suitable multiplicity procedure is applied. The complete correction strategy and hierarchy of secondary hypotheses are not reported in the registry record. Secondary outcomes are therefore useful as descriptive and supporting evidence, but their interpretation should remain cautious and separate from the sponsor’s primary-endpoint analysis.

Overall, the secondary measures can show whether the broader set of recorded outcomes points in a similar direction or presents a more mixed picture. They cannot establish that the primary endpoint’s pattern extends to every symptom measure, nor can the primary endpoint stand in for each secondary outcome. The endpoint-specific estimates and their uncertainty remain essential.

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

• Change From Baseline to End of Treatment in Mean Number of Micturitions Per 24 Hours
• Change From Baseline to End of Treatment in Mean Number of Incontinence Episodes Per 24 Hours
• Change From Baseline to Each Visit in Mean Volume Voided Per Micturition
• Change From Baseline to Each Visit in Mean Number of Micturitions Per 24 Hours
• Percentage of Participants With a Micturition Response
• Change From Baseline to Each Visit in Mean Number of Incontinence Episodes Per 24 Hours
• Percentage of Participants With Zero Incontinence Episodes Post-baseline
• Percentage of Participants With 50% Reduction in Incontinence Episodes

9. Statistical Interpretation

10. Statistical Methods Explained

What does a least-squares mean represent?

Least-squares means are model-based estimates of group means. In a clinical analysis, a model can account for specified features of the data and produce estimates that are not simply raw averages. The registry identifies the primary endpoint estimates as least-squares means and reports standard errors. It also lists ANCOVA as the method for the sponsor’s primary-endpoint comparisons. The exact covariates and full model specification are not reported in the registry record.

For example, the sponsor-reported comparison of placebo with solifenacin 5 mg is a least-squares mean difference of 22.0 mL, with a 95% confidence interval from 7.6 to 36.3 and p = 0.003. That comparison is model-based and should be distinguished from the simple recalculations based only on posted summary statistics. The adjusted analysis may use information not present in the arm summaries.

What does ANCOVA do?

General statistical explanation: analysis of covariance, or ANCOVA, compares groups while adjusting for covariates included in the model. Adjustment can improve precision when the covariates are informative and can account for baseline differences as specified in the analysis plan. The registry identifies ANCOVA for the reported primary comparisons, but the complete model specification and covariate list are not reported in the registry record. It is therefore not possible to reconstruct the sponsor’s model fully from the posted summaries alone.

How should the simple recalculations be viewed?

The recalculated comparisons use the displayed group summaries to form unadjusted differences and approximate uncertainty. The standard deviations used for that approximation are inferred from the posted standard errors, so they are not necessarily the original participant-level variability estimates. These recalculations do not adjust for covariates, account for the sponsor’s model, or reproduce any multiplicity procedure. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence.

General statistical explanation: an unadjusted comparison treats the contrast as a direct comparison of the displayed groups without incorporating other model terms. It is useful as a transparent check on the direction and rough scale of a result, but it should not override a prespecified adjusted analysis. Differences between an unadjusted calculation and an adjusted estimate can arise because the analyses use different information or assumptions.

Why does the endpoint’s scale matter?

The primary outcome is continuous and measured in mL. The estimated difference therefore remains in mL and can be read against the original measurement. The arm estimates describe mean change, and the sponsor’s comparison describes a difference in estimated mean change. A confidence interval expresses uncertainty about that contrast on the same scale. It does not by itself establish whether the magnitude is important to patients; a threshold for clinical importance is not reported in the registry record.

General statistical explanation: a continuous outcome retains more gradation than a binary outcome that reduces observations to categories. However, the usefulness of a continuous endpoint depends on how it is measured, how missing observations are handled, and whether the model fits the data. The registry describes diary collection and an analysis population requirement, but it does not report enough detail to assess every modeling assumption.

What is the role of the analysis population and imputation?

The stated Full Analysis Set includes participants who took at least one dose after randomization and had primary efficacy diary data at baseline and at least one post-baseline visit. The registry mentions last observation carried forward imputation, but the available description ends before explaining the full procedure. The exact number of participants contributing to each model and how missing data affected each estimate are not reported in the registry record.

General statistical explanation: imputation replaces or carries forward an observed value to address missing outcome data, but it relies on assumptions about what the unobserved measurements would have been. Different assumptions can affect estimates and uncertainty. A label such as last observation carried forward does not, by itself, show that missingness has been adequately addressed. Readers need the full protocol and analysis plan to assess the rationale and sensitivity analyses; those details are not reported in the registry record.

How should p-values be interpreted?

General statistical explanation: a p-value describes how compatible the observed data are with a specified null hypothesis under the analysis model. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. A p-value should be read alongside the effect estimate and confidence interval, and with attention to the number of comparisons. The registry record does not report a complete multiplicity strategy for the many arms and outcomes.

In this factorial, dose-ranging study, pairwise comparisons are only part of the statistical question. A factorial analysis might address whether the combined medicines behave differently from what would be expected from their separate contributions, but the registry record does not report such an interaction result. The available pairwise comparisons should therefore be interpreted as comparisons of the specific groups named, rather than as a complete analysis of combination effects.

11. Confidence Intervals and Precision

A confidence interval describes a range of values compatible with the data and the analysis, under its assumptions. The sponsor’s primary comparisons report 95% confidence intervals. Their width conveys precision: narrower intervals indicate less statistical uncertainty about the estimated contrast, while wider intervals leave more possible values compatible with the data. The interval does not account for every possible source of bias or uncertainty, such as missing-data assumptions or selective reporting.

For mirabegron 25 mg versus placebo, the reported difference is 11.0 mL and the 95% confidence interval runs from -5.6 to 27.6. Because this interval includes zero, the data are compatible with no difference as well as with differences in either direction under the reported analysis. For solifenacin 10 mg with mirabegron 50 mg versus placebo, the reported difference is 48.3 mL and the interval runs from 31.9 to 64.7. The interval is entirely above zero, indicating a positive estimated contrast under that model. These statements concern statistical uncertainty for those specific comparisons.

Some intervals are wider than others, reflecting different levels of precision across comparisons. Group sizes and standard errors also vary across the arms. The registry’s confidence intervals are model-based; the recalculated intervals are approximate and unadjusted, and should not be treated as interchangeable. The reported confidence intervals do not resolve whether a difference is clinically meaningful, since a clinically important threshold is not reported in the registry record.

General statistical explanation: a 95% confidence procedure would capture the true parameter in 95% of repeated samples if its assumptions held across repetitions. It is not a statement that there is a 95% probability that this particular interval contains the true value. Interpretation also needs to account for the collection of comparisons, since examining many intervals can increase the chance that some appear unusual by chance.

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 sample-size figures are planning illustrations based on the observed contrasts, not the original trial’s design calculations. For these continuous-outcome comparisons, the figures are participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned participants per arm for a design with an 80% chance of detecting the chosen effect under the stated assumptions, if that effect is real. The 90% power column describes the corresponding planning target for a 90% chance. These are design calculations and not observed power; they do not tell whether the trial’s observed result is true or whether a treatment effect exists.

Rows planning for a smaller fraction of the observed effect require more participants per arm. For instance, the table distinguishes planning for 100%, 75%, and 50% of the observed effect. This follows a general principle: smaller target differences are harder to distinguish from random variation, so a larger study is usually needed to detect them with the same planned power.

Read the figures as conditional illustrations, not as a recommendation for a future trial. They depend on the observed effect and approximate variability, and observed effects can be unstable. The assumptions do not show how the original study addressed multiple comparisons, missing data, or its factorial structure. The curve should be understood in the same planning context as the listed figures rather than as evidence about the power actually achieved.

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 = 10.900; pooled standard deviation σ = 52.846.
2. n = 2 × (1.96 + 0.842)² × 52.846² / 10.900² = 369.0, rounded up to 369 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 <- 10.9                      # observed difference in means
sigma <- 52.845653226496                     # 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(1340027)
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 = 369 (80% power), 494 (90% power)
 75% of observed effect: n per arm = 656 (80% power), 879 (90% power)
 50% of observed effect: n per arm = 1,476 (80% power), 1,976 (90% power)
power.t.test: 369.9 
Simulated power at n = 369 per arm: 0.801 (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 the sponsor’s own primary-endpoint comparisons using ANCOVA, including contrasts against placebo and selected contrasts against solifenacin 5 mg. Those estimates and confidence intervals are the study’s reported inferential analyses. The simple recalculations use posted arm summaries and approximate unadjusted uncertainty; they are not a reconstruction of the sponsor’s ANCOVA.

The record flags a discrepancy between the recalculations and the sponsor analysis. Where the two differ, the sponsor’s own analysis takes precedence. The recalculations can still help illustrate the relationship between the posted group summaries, but they should not be used to replace the adjusted estimates, their confidence intervals, or their p-values. In particular, the recalculated standard deviations are approximate, inferred from standard errors, and the calculations do not incorporate the sponsor model.

The sponsor’s reported comparisons should also be kept within their scope. They are pairwise contrasts for particular doses and endpoints. The registry record does not report a complete factorial interaction analysis or the full statistical plan, so the listed comparisons do not by themselves answer every question about the combined treatments.

15. Multiplicity, Missing Data and Analysis Populations

The trial includes multiple dose groups, combination regimens, comparisons, and outcomes. When many statistical tests are conducted, the chance of at least one apparently notable result arising by chance can increase. A multiplicity strategy may address this through a prespecified testing hierarchy, adjusted significance levels, or other procedures. The complete strategy for this study is not reported in the registry record, so the listed p-values should be read as reported rather than assumed to have been adjusted for all comparisons.

The registry identifies the primary endpoint and reports sponsor analyses, but it does not provide enough information to establish which contrasts were primary, secondary, or exploratory within the original statistical plan. It also does not report a complete factorial interaction analysis. Without those details, the pairwise contrasts cannot be treated as a comprehensive test of all dose and combination questions.

Missing-data reporting is also incomplete. The Full Analysis Set required a dose after randomization and baseline plus at least one post-baseline diary value. The registry mentions last observation carried forward imputation, but the description is truncated and does not explain the full implementation. The extent and pattern of missing data, and sensitivity analyses under alternative assumptions, are not reported in the registry record.

The outcome analysis population is not necessarily identical across endpoints; the posted secondary summaries show differing analysis counts. This makes it important to consider the endpoint-specific population and uncertainty rather than assuming every comparison represents the same participants. A detailed account of exclusions and missing observations by treatment group is not reported in the registry record.

These limitations do not invalidate the posted estimates, but they restrict how completely their robustness can be assessed. The protocol, full statistical analysis plan, and detailed missing-data analyses would be needed to evaluate the prespecification and handling of these issues.

16. Safety Results

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

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: abortion spontaneous (1.3%), confusional state (1.3%), pelvic pain (1.3%), muscular weakness (1.3%), foreign body trauma (1.2%).

The registry reports serious adverse events and a separate count of participants affected by other adverse events for each arm. Serious-event counts are low in the posted groups; the record includes zero in some arms and nonzero counts in others. For example, the placebo group reports 0 serious events, while mirabegron 50 mg reports 2. The other-event counts also vary across arms. These are counts of participants affected in the registry’s safety summaries, not estimates of comparative risk adjusted for differences between groups.

Deaths are not reported in the registry record. The listed serious-event terms include abortion spontaneous, confusional state, pelvic pain, muscular weakness, foreign body trauma, and abortion induced, each with a percentage printed in the registry. These terms should be read as reported event listings and not as a complete description of all safety outcomes.

Safety counts should be interpreted alongside the group-specific at-risk counts and the 12-week treatment period. They do not establish that the groups have equivalent safety profiles, particularly when events are uncommon and the study is a dose-ranging Phase 2 trial. The registry record does not provide enough information to assess the full event narratives, exposure-adjusted rates, or comparative statistical testing.

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

The primary endpoint records change in mean volume voided per micturition from baseline to Week 12. The registry’s sponsor analyses show positive estimated differences versus placebo for the listed active groups, with confidence intervals and p-values that vary by dose. This describes the posted results for this endpoint and study; it is not a conclusion about every symptom, every patient, or longer-term outcomes.

A statistically distinguishable estimate is not automatically a clinically important one. The registry record does not report a threshold for a clinically meaningful difference in this diary measure. Nor does a p-value determine whether an observed difference matters to participants. Those judgments require relevant clinical context that is not contained in the posted statistical summaries.

The study tested multiple doses and combinations over 12 weeks and included monotherapy and placebo groups. A pairwise contrast for a particular combination against placebo is not the same as a direct test of whether combining the medicines produces an interaction or an added effect beyond the individual medicines. Such an overall factorial result is not reported in the registry record.

The evidence should also be understood with the reported analysis population, imputation description, and multiplicity information in mind. The record’s incomplete account of missing-data handling and the absence of a complete multiplicity strategy limit a full assessment of robustness. The discrepancy flagged between simple recalculations and sponsor analyses further means that the sponsor’s model-based results, rather than approximate recalculations, should guide interpretation.

These results are specific to the enrolled study population, the diary endpoint, the treatment regimens, and the stated follow-up. They do not establish effects in other populations, for different durations, or on unreported outcomes. The safety figures are also separate evidence and should be considered alongside efficacy summaries rather than inferred from them.

18. Why This Trial Matters Statistically

This study is statistically informative because it compares several dose levels and combinations in a randomized factorial design, alongside monotherapy and placebo groups. That structure raises questions beyond whether any one arm differs from placebo: it also invites consideration of dose patterns and whether combinations behave differently from their components. The registry’s posted pairwise analyses address specific contrasts, while a complete interaction analysis is not reported in the registry record.

The study also illustrates why arm means and inferential comparisons must be distinguished. The displayed least-squares means describe estimated change in each group; the sponsor’s ANCOVA contrasts quantify differences between selected groups under a model. A simple recalculation from summary statistics can be a useful cross-check, but it cannot replace the adjusted analysis, particularly when the record flags a discrepancy.

Interpretation also depends on precision and multiplicity. Confidence intervals communicate uncertainty for individual comparisons, while the number of arms and outcomes makes it important to know whether and how the testing plan controlled repeated comparisons. The full plan is not reported in the registry record. Secondary findings can broaden the clinical picture, but they should not be treated as equally confirmatory without that context.

Finally, the analysis population and diary-based measurement show how data availability and outcome definition shape the evidence. The registry describes the primary measure and its collection period, but its imputation description is incomplete. Reading the results with these methodological limits in mind helps separate what the reported analyses establish from what remains unresolved.

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’s description of the Full Analysis Set is followed by an incomplete sentence about last observation carried forward imputation. This leaves the complete missing-data procedure unclear. The record does not report sensitivity analyses or a detailed account of missing observations by group, limiting assessment of how missing data may influence the endpoint estimates.

The sponsor reports ANCOVA comparisons, but the full model specification, including covariates, is not reported in the registry record. The simple recalculations use approximate standard deviations inferred from standard errors and are unadjusted; the record flags a discrepancy, so they should not be treated as replacements for the sponsor results.

The study has numerous arms and outcomes. A complete multiplicity procedure and testing hierarchy are not reported in the registry record. The reported pairwise comparisons therefore need to be interpreted with caution, particularly outside the primary endpoint. The registry also does not report a full factorial interaction analysis, limiting conclusions about whether combinations have effects beyond their individual components.

The primary outcome is based on diary observations over 3 days before baseline and Week 12 visits. The registry does not report details needed to assess diary adherence or the full handling of the repeated observations. The clinical importance threshold for the primary measure is also not reported in the registry record.

Finally, follow-up for the described treatment period is 12 weeks. The posted primary endpoint and safety summaries do not establish longer-term outcomes. The safety record does not report deaths, and the available event counts alone do not provide a complete comparative safety assessment.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy, Safety and Tolerability of Mirabegron and Solifenacin Succinate Alone and in Combination for the Treatment of Overactive Bladder — NCT01340027.
• Registry record last updated 2024-10-31; status last verified 2024-10.
• Results first posted 2015-07-21.
• 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

NCT01340027 is a completed Phase 2 randomized, triple-masked, factorial, parallel-group study sponsored by Astellas Pharma Europe B.V. It enrolled 1307 participants and compared placebo, mirabegron, solifenacin, and six combinations over 12 weeks.

The primary endpoint was change from baseline to Week 12 in mean volume voided per micturition, derived from participant diaries. Sponsor-reported ANCOVA comparisons include placebo contrasts and selected comparisons with solifenacin 5 mg. The registry also lists secondary symptom outcomes and safety counts.

Recalculated comparisons are approximate and unadjusted; the registry flags a discrepancy, so the sponsor’s own analysis takes precedence. Details of multiplicity handling, the complete missing-data procedure, original sample-size justification, and a full factorial interaction analysis are not reported in the registry record.