Behavioral or Solifenacin Therapy for Urinary Symptoms in Parkinson Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Behavioral or Solifenacin Therapy for Urinary Symptoms in Parkinson Disease (NCT03149809), a randomized phase 3 study. The primary outcome is ICIQ-OAB Questionnaire.

2. Clinical Question

The clinical rationale in the registry links urinary symptoms in Parkinson disease with burdens such as urgency, incontinence, nocturia, falls, caregiver stress, and disability. It also notes concern about anticholinergic medications in the context of cognitive and autonomic burdens. Those statements describe the rationale for studying alternatives; they are not outcomes established by the posted trial results. The central statistical task is therefore narrower: interpret the measured symptom score and its uncertainty, while keeping the trial's stated non-inferiority aim distinct from what the reported comparison can demonstrate.

3. Trial Design

The registry describes a randomized, single-masked, parallel-group phase 3 trial, now listed as completed. The study title is “Behavioral or Solifenacin Therapy for Urinary Symptoms in Parkinson Disease.” The sponsor is the VA Office of Research and Development. The registry lists an enrollment of 77, a start date of 2018-03-01, and a primary completion date of 2023-09-08.

Participants were assigned to pelvic floor muscle exercise-based behavioral therapy or daily solifenacin drug therapy. The primary endpoint was the ICIQ-OAB symptom score at 12 weeks. Its posted analysis includes 36 participants in the behavioral group and 41 in the drug group. Multiple imputation methods were used to account for missing data in the primary outcome, although the imputation procedures and assumptions are not reported in the registry record.

The registry identifies the study as using a non-inferiority design in its description of the project. However, the non-inferiority margin, original sample-size assumptions, masking details, allocation procedures, and analysis plan are not reported in the registry record. The posted primary comparison is a difference in group means with a confidence interval and an unadjusted p-value; the record does not identify it as a formal non-inferiority test. Thus, the design description and the specific information available for interpreting the posted result should be kept separate.

The registry also lists a bladder diary outcome and an ICIQ-OAB quality-of-life outcome, both assessed at 12 weeks. The outcome-specific analysis counts differ: the bladder diary result includes 21 participants in the behavioral group and 27 in the drug group, while the quality-of-life result includes 36 and 41, respectively. Reasons for these differences are not reported in the registry record. The record lists no reported analyses for the secondary outcomes.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Multiple imputation methods used to account for 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.

6. Primary Endpoint

The registry lists the primary outcome as ICIQ-OAB Questionnaire, measured over ICIQ-OAB Symptom score at 12 weeks.

The primary endpoint was the ICIQ-OAB questionnaire symptom score at 12 weeks. The registry describes this measure as a four-question assessment of overactive bladder symptoms and how much they bother the respondent. The questions cover urgency, frequency, nocturia, and urinary incontinence. It is therefore a patient-reported measure combining symptom experience with the degree of bother, rather than a direct count of every urinary event.

A standardized questionnaire can make outcomes comparable across treatment groups by applying the same questions and scoring approach to each group. It can also capture the respondent’s experience, which may not be fully represented by a diary count alone. In this trial, the primary result is presented as a group mean and standard deviation for each treatment, together with a mean difference and confidence interval.

The registry calls the outcome a score on a scale, but does not report the score range, the direction associated with improvement, a threshold for a clinically important change, or a non-inferiority margin. Those details matter when translating a numerical contrast into clinical meaning. The observed group averages and their uncertainty can be described, but the registry record does not support labeling a particular score difference as clinically important or as meeting a non-inferiority criterion.

7. Results Posted in the Registry

• Drug Therapy: mean 5.80 versus 5.50 on control; difference 0.30 (95% CI -0.68 to 1.28), standardized effect d = 0.13; z-test p = 0.550.

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.

Bladder Diary

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • Drug Therapy: 0.86 versus 0.45 (Incontinence episodes per day) on control; rate ratio 1.91 (95% CI 1.76–2.08, approximate, Poisson model); p ≈ <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically higher for Drug Therapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

ICIQ-OAB QOL

• 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:
  • Drug Therapy: mean 56.80 versus 56.60 on control; difference 0.20 (95% CI -10.70 to 11.10), standardized effect d = 0.01; z-test p = 0.971.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Drug Therapy and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address related but distinct aspects of urinary symptoms: a bladder diary measure of incontinence episodes per day and an ICIQ-OAB quality-of-life score at 12 weeks. Across them, the posted pattern is not uniform in measurement or statistical form. One is presented as a rate comparison, while the other is a difference between group means. These measures can complement the primary symptom questionnaire, but they do not measure exactly the same construct and should not be expected to produce identical estimates.

The primary endpoint is the ICIQ-OAB symptom score, so secondary findings are contextual rather than replacements for that primary result. A secondary endpoint may offer useful supporting information, but an isolated result should not override the primary estimate and its uncertainty. Interpretation should consider the outcome definition, the available analysis counts, and the different statistical models. The registry does not report analyses that formally combine the secondary findings with the primary result.

The record lists no reported analyses for the secondary outcomes, and the displayed secondary comparisons are unadjusted. When several outcomes are tested, the chance of at least one apparently notable result can increase, even if none represents a reliable underlying effect. A prespecified multiplicity strategy can address that issue, but one is not reported in the registry record. The unadjusted secondary results consequently carry less inferential weight than results supported by a prespecified analysis plan and an explicit approach to multiple testing.

Analysis counts also vary across outcomes. The registry does not explain why fewer participants contribute to the diary result than to the primary outcome or quality-of-life result. That limits assessment of whether the secondary results reflect the same participant group and whether missing observations could influence the pattern. The secondary measures can be read as additional descriptive evidence, with caution about statistical multiplicity, model assumptions, and outcome availability.

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

• Bladder Diary
• ICIQ-OAB QOL

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish what the registry reports from what can be concluded from it. The primary endpoint is a continuous questionnaire score, summarized by a mean and standard deviation in each treatment group. The posted comparison is a mean difference. A mean difference expresses the contrast between group averages in the original score units; it does not describe every participant’s response, the spread of individual changes, or the proportion who improved. The direction of better scores is not reported in the registry record, so the sign of the contrast should be stated without assigning a benefit label.

What does the confidence interval describe?

A confidence interval gives a range of estimates compatible with the observed data under the statistical model and its assumptions. It conveys uncertainty about the group contrast, not the range of individual scores and not the probability that the true effect lies in one particular interval. For the primary mean difference, the posted interval extends from -0.683 to 1.283. Because zero lies within that interval, the data do not distinguish the group means at conventional two-sided significance thresholds. The interval’s span also means that the point estimate should not be treated as exact. Whether the values in the interval are clinically important cannot be determined without a score interpretation or meaningful-difference threshold, neither of which is reported.

How should the p-value be read?

The primary unadjusted p-value is 0.55. In general, a p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the model assumptions were true. It does not give the probability that the null hypothesis is true, and it does not measure clinical importance. A relatively large p-value is not evidence that the groups are identical. The interval and estimate provide more information about the direction and plausible scale of the contrast than the p-value alone.

What is different about the diary outcome?

The bladder diary outcome is reported as incontinence episodes per day, with group means and standard deviations, while its posted comparison is a rate ratio. A rate ratio compares event rates, rather than subtracting group means. General statistical explanation: a Poisson model is often used for counts or rates, with the amount of time observed incorporated as exposure. Such models rely on assumptions about the relationship between the mean and variance of counts. Over-dispersion means that observed variability exceeds what a Poisson model allows; when present and unaccounted for, uncertainty can be understated and inference can be too confident. The registry identifies a Poisson analysis, but does not report an over-dispersion assessment or adjustment. The listed event and exposure quantities and the analysis details should therefore be interpreted as posted, not as a fully documented model specification.

The diary comparison reports a rate ratio of 1.911, a confidence interval from 1.76 to 2.075, and an unadjusted p-value of <0.001. For a rate ratio comparing drug therapy with behavioral therapy, a value above one indicates a higher estimated rate in the drug group relative to the behavioral group. This is a description of the posted contrast, not an explanation of why the rates differ or proof of a causal mechanism. Its interpretation also depends on the rate model and its assumptions.

Why do analysis populations and missing data matter?

The primary outcome description says multiple imputation was used to account for missing data. In general, multiple imputation creates several completed versions of an incomplete dataset, analyzes each, and combines the results so that uncertainty from imputation is reflected. Validity depends on the imputation model and assumptions about missingness. The registry does not report the model, variables included, missingness pattern, or sensitivity analyses. It is therefore not possible to assess how robust the result is to departures from the imputation assumptions.

The outcome-specific analysis counts also differ, particularly for the bladder diary. These differences could reflect availability of outcome data or other analysis-population rules, but their causes are not reported in the registry record. The recorded counts should not be assumed to represent the same analysis population across outcomes. The record does not report an intention-to-treat definition, per-protocol population, adherence analysis, or how participants were handled after randomization.

What do the planning illustrations mean?

Planning figures based on an observed effect are illustrative calculations, not a reconstruction of the trial’s original design. The assumptions listed are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect targeted is a stated fraction of the observed effect. For the rate outcome, the planning convention is based on total events, while the other planning figures are participants per arm. General statistical explanation: under a fixed design and other assumptions, planning to detect a smaller effect usually requires more information, commonly through more participants or events. These calculations do not establish that the trial had adequate power for its original question, and the original sample-size justification is not reported in the registry record.

Finally, the primary comparison is not identified in the registry record as adjusted for additional covariates, and no multiplicity strategy is described. The reported p-value is explicitly unadjusted. Statistical interpretation should remain tied to that reporting: a group-level estimate, its uncertainty, and the stated analysis method, without adding assumptions about unreported modeling choices.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of 0.3 for drug therapy relative to behavioral therapy. Its 95% confidence interval, from -0.683 to 1.283, includes zero and extends in both directions. This means the observed data are compatible with a range of possible group contrasts under the analysis assumptions, rather than identifying a single precise value. The interval does not establish that the treatments are the same, and it does not by itself determine whether any possible difference is clinically important.

The group standard deviations were 2.0 for behavioral therapy and 2.4 for drug therapy. Standard deviations describe variation among observed scores within each group; they are not confidence limits around the group means. The group analysis counts were 36 and 41, and the registry indicates that multiple imputation was used for the primary outcome. The record does not provide the missingness pattern or enough imputation details to assess how those procedures affect precision under alternative assumptions.

The interval can be used to distinguish statistical uncertainty from the point estimate. A point estimate near zero accompanied by an interval that crosses zero is not evidence of equivalence. For a non-inferiority interpretation, the interval would need to be assessed against a prespecified margin, and that margin is not reported in the registry record. No clinical importance threshold for the ICIQ-OAB score is reported either. The available precision information therefore supports a cautious account of the observed contrast, but not a definitive claim about practical similarity or non-inferiority.

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 illustrations based on the observed effect, not the trial’s original design assumptions. The listed calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a stated fraction of the observed effect as the effect to detect. The original sample-size justification and design assumptions are not reported in the registry record.

For the continuous outcomes, the figures are participants per arm. For the bladder diary rate outcome, the planning convention is the total number of events, not participants per arm. This distinction matters: event-based planning depends on event information, while participant-based planning describes how many people would be assigned to each group under the stated allocation assumption.

The 80% power column describes the planned chance of rejecting the specified null hypothesis under the assumed effect and model if the study were repeated under those conditions. The 90% power column uses a higher target chance of detecting that effect, with other assumptions held as specified. These are design targets, not guarantees about what an individual study will show. Smaller effects require more information to detect reliably, so the planning figures increase when the target is a smaller fraction of the observed effect.

These calculations are not observed power. They are hypothetical planning illustrations tied to estimated effects and simplified assumptions. They should not be used to infer why enrollment took the value recorded, whether the original design was adequate, or what the trial’s actual probability of detecting an effect was. The registry record does not report the original design’s sample-size rationale or a formal power analysis.

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 = 0.300; pooled standard deviation σ = 2.222.
2. n = 2 × (1.96 + 0.842)² × 2.222² / 0.300² = 861.4, rounded up to 862 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 <- 0.3                      # observed difference in means
sigma <- 2.2223111093334                     # 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(3149809)
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 = 862 (80% power), 1,154 (90% power)
 75% of observed effect: n per arm = 1,532 (80% power), 2,051 (90% power)
 50% of observed effect: n per arm = 3,446 (80% power), 4,613 (90% power)
power.t.test: 862.4 
Simulated power at n = 862 per arm: 0.800 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, contrasts, or analyses are considered. Even when each individual test uses a conventional significance threshold, examining multiple results can increase the chance of at least one result appearing statistically notable by chance. This is why trial interpretation depends on which endpoint was primary, which analyses were planned, and whether any adjustment or hierarchy was specified. The registry identifies the ICIQ-OAB symptom score as the primary endpoint and lists two secondary outcomes. It does not report a multiplicity adjustment, a testing hierarchy, or a detailed statistical analysis plan. The secondary p-values are unadjusted and should be treated accordingly.

The registry’s project description identifies a non-inferiority design, but the non-inferiority margin and formal analysis are not reported in the registry record. A non-inferiority design typically needs a clinically justified margin established in advance and an analysis that compares the confidence interval with that margin. Without the margin and analysis details, the primary difference and its confidence interval cannot establish non-inferiority. The absence of these details in the record does not show that no such planning occurred; it means the posted information does not document it.

For the primary endpoint, the registry states that multiple imputation was used to account for missing data. Multiple imputation can incorporate uncertainty associated with missing values, but its validity depends on the model and assumptions. The amount and pattern of missingness, variables used in imputation, number of imputed datasets, diagnostics, and sensitivity analyses are not reported in the registry record. It is therefore not possible to determine from the record how well the imputation assumptions fit the observed data or how results might change under alternative missing-data assumptions.

The registry does not describe the analysis populations, such as an intention-to-treat or per-protocol population, or the handling of deviations from assigned treatment. That information is particularly relevant to interpreting a non-inferiority study, where different analysis populations can inform robustness. Outcome-specific participant counts vary, and the reasons are not reported. No assumptions should be made about whether missing observations reflect withdrawal, unavailable assessments, or another cause.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: fall (4.9%), edema (4.9%), foot sore (4.9%), pneumonia (2.8%).

The registry reports serious adverse events among 36 participants at risk in the behavioral therapy group and 41 at risk in the drug therapy group. The reported serious adverse event counts were 1 and 6, respectively. Other adverse events were reported for 0 and 4 participants, respectively. Deaths were reported as 0 in each group. These are event counts as recorded; they do not establish that an event was caused by the assigned treatment.

The registry also lists serious adverse event terms with percentages: Fall, 4.9%; Edema, 4.9%; Foot sore, 4.9%; and Pneumonia, 2.8%. The record does not provide additional detail in these summaries about timing, severity beyond the serious classification, recurrence, or attribution. The percentages should be read as the registry lists them, without deriving additional rates or assuming that every event has the same clinical context.

Safety counts are descriptive and should be interpreted alongside the study’s size, follow-up, event definitions, and ascertainment procedures. The registry does not report enough detail to evaluate comparative safety formally or to determine whether differences in counts reflect treatment, chance, or other factors. These figures are not a basis for individual treatment decisions.

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

The posted results describe a randomized comparison of behavioral therapy and daily solifenacin for urinary symptoms in Parkinson disease. For the primary ICIQ-OAB symptom score at 12 weeks, the observed group means were close, and the estimated mean difference was accompanied by a confidence interval that includes zero. This is evidence that the registry’s primary comparison did not clearly distinguish the group averages under the posted analysis. It is not proof that the treatments are identical or that any possible difference is unimportant.

The registry describes a non-inferiority aim, but a conclusion about non-inferiority requires a prespecified margin and a suitable analysis. Those details are not reported in the registry record. A non-significant difference test is not a substitute for that assessment. The result therefore should not be restated as showing that behavioral therapy is non-inferior, equivalent, or interchangeable with drug therapy.

The secondary outcomes and adverse event counts add information about other measured outcomes and reported events, but they have limitations. The secondary analyses are unadjusted, and no multiplicity plan is reported. Their outcome-specific analysis counts differ, with reasons not reported. The safety summaries are descriptive and do not establish causation. In addition, the record does not report a clinically important threshold for the primary score, the score direction associated with improvement, or detailed missing-data sensitivity analyses.

These results are most appropriately read as estimates from the posted trial record, with uncertainty and reporting gaps kept visible. They do not establish which approach is preferable for an individual, and they do not provide medical advice. Further interpretation would require details such as the non-inferiority margin, analysis populations, missing-data assumptions, and fuller trial reporting. The statistical evidence supports a measured description of the observed comparisons rather than a broad claim about treatment effectiveness.

17. Why This Trial Matters Statistically

This trial raises an important statistical distinction: a study described as non-inferiority cannot be interpreted through a conventional difference test alone. The primary comparison reports a mean difference and confidence interval, but the registry does not report the non-inferiority margin or a formal non-inferiority analysis. Making that distinction prevents a non-significant p-value from being mistaken for evidence that two treatments are sufficiently similar.

The trial also illustrates why endpoint definition matters. The primary questionnaire measures symptoms and bother, while the diary records incontinence episodes per day and the quality-of-life measure captures another aspect of participants’ experience. These endpoints differ in scale, analysis model, and potentially in who contributed data. Treating them as interchangeable would obscure what each analysis estimates.

Precision is another central issue. The primary estimate is close to zero, but its confidence interval spans both negative and positive values. That interval communicates uncertainty more fully than the point estimate or p-value alone. A clinical interpretation also requires a score direction and a threshold for meaningful change, neither of which is reported in the registry record.

Finally, the record highlights the importance of transparent reporting. Multiple imputation is noted, but its assumptions and sensitivity analyses are not. Secondary results are unadjusted, and no multiplicity strategy is described. These gaps do not establish that the original investigators lacked a plan; they limit what can be evaluated from the registry record. Careful interpretation separates what was measured and reported from what would require additional documentation.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several trial-specific limitations in the registry record constrain interpretation. Although the project description calls the design non-inferiority, the record does not report the non-inferiority margin, the rationale for that margin, or a formal analysis against it. The primary mean-difference result therefore cannot be treated as a completed non-inferiority assessment. The original sample-size justification and design assumptions are also not reported. Planning illustrations based on the observed effect do not fill that gap.

The record does not identify who was masked, despite listing single masking. It does not describe the randomization sequence, allocation concealment, adherence, treatment deviations, or analysis populations. These omissions limit assessment of implementation and of whether the posted comparisons correspond to an intention-to-treat or per-protocol analysis.

Missing-data information is limited. Multiple imputation is stated for the primary endpoint, but the missingness pattern, imputation model, and sensitivity analyses are not reported. Outcome-specific analysis counts differ, particularly for the diary outcome, without an explanation of the reasons. The registry also does not report a score direction or clinical-importance threshold for the primary questionnaire.

The secondary findings require additional caution because they are unadjusted and the registry does not report a multiplicity strategy. The diary analysis is identified as Poisson, but assessment or handling of over-dispersion is not reported. Safety summaries lack detail about event timing, attribution, and ascertainment. These reporting limits do not prove that relevant procedures or analyses were absent; they mean the registry record does not permit their evaluation.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Behavioral or Solifenacin Therapy for Urinary Symptoms in Parkinson Disease — NCT03149809.
• Registry record last updated 2024-09-24; status last verified 2024-08.
• Results first posted 2024-09-24.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The completed registry entry describes a randomized, single-masked, parallel-group phase 3 comparison of pelvic floor muscle exercise-based behavioral therapy with daily solifenacin for urinary symptoms in Parkinson disease. Enrollment is listed as 77, and the primary endpoint is the ICIQ-OAB symptom score at 12 weeks. The posted primary analysis reports a mean difference of 0.3, with a 95% confidence interval from -0.683 to 1.283 and an unadjusted p-value of 0.55.

The registry also reports a bladder diary outcome, an ICIQ-OAB quality-of-life outcome, and adverse event summaries. The project description identifies a non-inferiority design, but the margin and formal non-inferiority analysis are not reported in the registry record. Multiple imputation is noted for the primary endpoint; details of the procedure, analysis populations, and multiplicity strategy are not reported.