Efficacy of Botulinum Toxin Type A for the Treatment of Non-neurogenic Urinary Urge Incontinence: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of Botulinum Toxin Type A for the Treatment of Non-neurogenic Urinary Urge Incontinence (NCT01226706), a randomized na study. The primary outcome is Change in Maximum Capacity at Cystoscopy Between Baseline and 6 Month Follow-up.

2. Clinical Question

The trial addressed whether botulinum toxin A was associated with a different change in maximum bladder capacity than placebo in people with non-neurogenic urinary urge incontinence. Maximum capacity was measured under anesthesia, as described in the registry record. The primary outcome was a change score from baseline to the 6-month follow-up, rather than a measure of everyday bladder capacity or a direct count of incontinence episodes.

The registry also identifies side effects and quality of life as secondary objectives. Listed secondary outcomes include changes in incontinence episodes and daytime voids at follow-up times. Those outcomes are relevant to the trial's broader aims, but they do not replace the stated primary question. The record does not provide detailed eligibility criteria, participants' prior treatment histories, or a fuller description of how quality of life was measured, so the clinical question cannot be narrowed beyond the non-neurogenic urinary urge incontinence population and outcomes recorded.

3. Trial Design

The registry describes a randomized, double-blind, placebo-controlled trial with a crossover model. It is listed as completed, with an enrollment of 21. The study dates recorded are 2008-06 for the start and 2010-09 for primary completion. The registry lists no applicable phase.

The intervention was botulinum toxin type A, described as 100U injected into the detrusor at Day 1. The comparator was placebo injected into the detrusor at Day 1. The double-blind designation indicates that the registry classifies the study as masked for two parties, but it does not identify those parties or describe how masking was maintained. Further details of the randomization procedure are not reported in the registry record.

The crossover classification matters for interpreting the design: in a crossover study, participants may contribute observations under more than one treatment condition, and period or within-participant structure can affect analysis. However, the registry record does not report the treatment sequence, timing of periods, washout procedures, or whether all participants completed both conditions. It also does not explain how the crossover structure was incorporated into the posted primary comparison. The posted arm summaries list 10 for placebo and 11 for botulinum toxin type A, but they do not by themselves clarify the participant flow or analysis population.

The record lists 39 outcome measures and 27 analyses, and reports 38 secondary outcomes as posted. The original statistical plan, sample-size justification, planned handling of repeated measurements, and analysis-population definitions are not reported in the registry record. The planning illustrations are based on observed results rather than the original trial design assumptions.

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

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 Change in Maximum Capacity at Cystoscopy Between Baseline and 6 Month Follow-up, measured over Baseline to 6 months.

The primary endpoint is change in maximum capacity at cystoscopy between baseline and the 6-month follow-up. Cystoscopy uses a narrow tube with a camera to view the inside of the bladder and urethra. The registry defines maximum bladder capacity as the amount of liquid or gas the bladder can hold under anesthesia; without anesthesia, pain or a strong urge can limit the amount measured.

This measurement offers a physiological outcome related to bladder storage capacity. Measuring under anesthesia is intended to assess capacity without the usual conscious sensations of pain or urgency determining when the measurement stops. It is therefore distinct from a diary-based measure of everyday urgency, daytime voids, or incontinence episodes. A change score compares the follow-up measurement with the baseline measurement, so the group summaries describe the recorded change over that interval.

The endpoint is useful for addressing the trial's stated question about bladder capacity, but it should not be treated as a complete measure of symptom burden or quality of life. The record does not report a threshold for a clinically important change, nor does it explain how a change in capacity relates to the outcomes participants might notice in daily life. The result consequently describes the recorded physiological measure and its statistical uncertainty, not by itself the full clinical experience of participants.

7. Results Posted in the Registry

• Botulinum Toxin Type A: mean 64.10 versus -97.50 on control; difference 161.60 (95% CI 35.56 to 287.64), standardized effect d = 1.12; z-test p = 0.012.

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 in Incontinence Episodes Between Baseline and 6 Week Follow-up

• 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:
  • Botulinum Toxin Type A: mean 3.00 versus 0.50 on control; difference 2.50 (95% CI -0.59 to 5.59), standardized effect d = 0.67; z-test p = 0.113.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Botulinum Toxin Type A and the control. The interval gives the range of effects that remain compatible with the data.

Change in Incontinence Episodes Between Baseline and 3 Month Follow-up

• 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:
  • Botulinum Toxin Type A: mean 5.05 versus 1.28 on control; difference 3.77 (95% CI 0.42 to 7.12), standardized effect d = 0.93; z-test p = 0.027.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Botulinum Toxin Type A than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Incontinence Episodes Between Baseline and 6 Month Follow-up

• 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:
  • Botulinum Toxin Type A: mean 4.09 versus -0.39 on control; difference 4.48 (95% CI 0.65 to 8.31), standardized effect d = 0.98; z-test p = 0.022.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Botulinum Toxin Type A than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the picture beyond cystoscopic bladder capacity, including incontinence episodes and daytime voids at selected follow-up times. Across the posted episode summaries, the botulinum toxin type A group has larger mean changes than the placebo group at each of the episode time points described. However, the record does not clearly specify the direction that a positive change represents, so these values alone cannot establish whether the change corresponds to fewer episodes or a more favorable symptom pattern.

The unadjusted comparisons and sponsor-reported analyses do not provide a consistent basis for treating the secondary outcomes as confirmation of the primary result. The sponsor's reported p-values for the episode outcomes differ from the recalculated p-values, reflecting the different statistical summaries and methods. Some intervals from the recalculations include zero, while others do not, but those calculations do not account for the full uncertainty about analysis structure or multiple testing.

General explanation: secondary outcomes often help assess whether a primary result is accompanied by changes in other aspects of the condition. But when many outcomes and analyses are examined, the chance of finding apparently unusual results somewhere among them increases unless the analysis plan accounts for multiplicity. The registry lists 39 outcome measures and 27 analyses, and 38 secondary outcomes are posted. A multiplicity adjustment or a prespecified hierarchy is not reported in the registry record. Consequently, unadjusted secondary findings carry less weight than a clearly prespecified primary comparison and should be considered exploratory.

The registry also lists quality of life as a secondary objective, but the registry entries do not give a detailed quality-of-life result to interpret. Nor do they provide the same full set of numerical details for every posted secondary outcome. The overall secondary pattern therefore offers context, not a decisive extension of the primary finding.

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

• Change in Incontinence Episodes Between Baseline and 6 Week Follow-up
• Change in Incontinence Episodes Between Baseline and 3 Month Follow-up
• Change in Incontinence Episodes Between Baseline and 6 Month Follow-up
• Change in Incontinence Episodes Between Baseline and 9 Month Follow-up
• Change in Incontinence Episodes Between Baseline and 12 Month Follow-up
• Change in Incontinence Episodes Between Baseline and 24 Months Follow-up
• Change in Number of Daytime Voids Between Baseline and 6 Week Follow-up
• Change in Number of Daytime Voids Between Baseline and 3 Month Follow-up

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean difference describe?

The primary endpoint is continuous: each participant's outcome is a measured change in maximum capacity, expressed in mL. A group mean describes the average recorded change among the participants summarized in that group. The recalculated mean difference of 161.6 mL is the botulinum toxin type A group mean change compared with the placebo group mean change. It is a difference between group averages, not the change experienced by every participant and not an adjusted estimate accounting for other variables.

A mean difference can be informative when the measurement is meaningful on its original scale. The units retain their clinical interpretation, unlike a standardized effect size. However, an average alone does not show how individual observations were distributed. The group standard deviations, 176.9 mL for placebo and 105.2 mL for botulinum toxin type A, indicate substantial variation in the observed changes relative to the means. The registry does not provide individual-level values or a distribution plot in the registry record for these explanations, so the shape of those distributions cannot be characterized.

What is a confidence interval?

General explanation: a confidence interval describes the statistical uncertainty around an estimated quantity under the assumptions of the method used. The primary recalculated 95% interval extends from 35.56 to 287.6 mL for the mean difference. Its lower and upper limits are both above zero, indicating that the interval of estimates compatible with this calculation does not include no difference. The interval is still broad enough to include a range of possible magnitudes, so the point estimate should not be read as exact. A confidence interval is not a guarantee that the true value lies within these particular limits, and it does not account for design or analysis problems that are not represented in the calculation.

How do the two p-values relate?

The registry reports the sponsor's primary analysis as Wilcoxon (Mann-Whitney), with p = .016. The recalculated p-value is 0.012 and comes from a simple, unadjusted comparison derived from posted summary statistics. The Wilcoxon (Mann-Whitney) procedure is rank-based; it evaluates a difference in the distribution of ranks between groups rather than directly estimating the difference in means. The recalculated analysis instead focuses on the mean difference and its interval. Because the methods and target quantities differ, their p-values need not match. Neither p-value is the probability that the null hypothesis is true, nor does either quantify the probability that the result occurred by chance in an everyday sense.

The registry labels the trial model as crossover, while the reported sponsor method is identified as Wilcoxon (Mann-Whitney), a comparison of two groups. The record does not report the sequence, period structure, or whether a paired or other crossover-aware procedure was used. General explanation: when observations from the same participant are related across treatment periods, an analysis that treats them as independent can fail to represent that dependence. The available summary does not establish whether that issue applies to the posted analysis, so no specific correction can be inferred.

Why does variability matter?

General explanation: variability affects how precisely a group mean and a difference between means can be estimated. More spread in measurements generally makes an estimate less precise when other features are similar. The observed standard deviations are large in relation to the small group summaries, and the resulting primary confidence interval spans a substantial range of possible mean differences. The registry does not report an adjusted model or covariates that might account for variation.

General explanation: over-dispersion occurs when the observed variation is greater than an analysis model expects. If a count outcome is more variable than its assumed distribution allows, standard errors may be too small and statistical evidence may appear stronger than it is. Incontinence episodes are count-like outcomes, but the registry's posted information does not report a model for those counts or an assessment of over-dispersion. It is therefore appropriate to raise this as a general consideration, not to assert that over-dispersion occurred in this trial.

The displayed recalculations are unadjusted and rely on posted summary statistics. They do not incorporate individual-level data, potential period effects, baseline covariates, or missingness adjustments. Those details are not reported in the registry record. Interpretation should therefore distinguish the calculation that can be made from the summaries from the trial's full analysis plan, which is not available in the record.

11. Confidence Intervals and Precision

The primary mean difference is 161.6 mL, and its 95% confidence interval runs from 35.56 to 287.6 mL. This interval excludes zero under the recalculation, but its width shows that the effect magnitude is not pinned down precisely. Estimates nearer the lower limit and estimates nearer the upper limit would imply quite different sizes of group difference, even though both are compatible with the interval calculation.

The underlying group summaries are based on 10 in the placebo group and 11 in the botulinum toxin type A group. The posted standard deviations are 176.9 mL and 105.2 mL, respectively. These figures help explain why a statistically positive comparison should not be confused with a highly precise estimate. The interval expresses sampling uncertainty for the mean difference under the recalculation's assumptions; it does not capture uncertainty from missing data, possible crossover-period effects, outcome selection, or an unreported analysis population.

The sponsor's reported primary result gives p = .016 from a Wilcoxon (Mann-Whitney) analysis, but no effect estimate or confidence interval is reported for that analysis. The recalculated interval applies to the mean difference from posted summaries, not to the rank-based analysis. It should not be attributed to the sponsor's method.

General explanation: a confidence interval is most useful when considered alongside the point estimate, the measurement scale, and the design. Statistical compatibility with a difference does not establish that the full range of plausible effects is clinically important. The registry record does not report a threshold for a meaningful change in maximum capacity, so clinical importance cannot be judged from the interval alone.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. They apply to illustrations based on the observed primary effect and do not describe the trial's original sample-size rationale. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each illustration asks how many participants per arm would be needed if the effect to detect were the stated fraction of the observed effect.

The 80% power column represents the planned ability to detect the specified effect in 80% of repeated studies under those assumptions, if that effect were the true one and the analysis assumptions held. The 90% power column uses a higher target probability of detecting that same specified effect. These are design-planning concepts, not guarantees about the result of a future study. The original trial's design assumptions and sample-size justification are not reported in the registry record.

The rows planning for 100%, 75%, and 50% of the observed effect illustrate how the assumed target effect changes the required sample size. A smaller effect is harder to distinguish from random variation and therefore requires more participants for the same target power under otherwise comparable assumptions. These planning calculations are not observed power: observed power is not a useful way to summarize what the completed trial found, and the illustrations should not be read as an estimate of the trial's probability of detecting an effect after the results are known.

The illustrations also do not address features not included in the stated assumptions, such as the crossover structure, missing outcomes, or multiplicity. The original design may have used other assumptions, but those are not reported in the registry record. The figures are best used to understand the scale of a hypothetical future design under the stated simplified conditions, not as a reconstruction of the trial's intended enrollment.

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 = 161.600; pooled standard deviation σ = 143.691.
2. n = 2 × (1.96 + 0.842)² × 143.691² / 161.600² = 12.4, rounded up to 13 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 <- 161.6                      # observed difference in means
sigma <- 143.690536186186                     # 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(1226706)
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 = 13 (80% power), 17 (90% power)
 75% of observed effect: n per arm = 23 (80% power), 30 (90% power)
 50% of observed effect: n per arm = 50 (80% power), 67 (90% power)
power.t.test: 13.4 
Simulated power at n = 13 per arm: 0.782 (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's own primary analysis is reported as Wilcoxon (Mann-Whitney), with p = .016. The recalculated result is an unadjusted mean difference of 161.6 mL, with a 95% confidence interval from 35.56 to 287.6 mL and p = 0.012. These should be read as results from different statistical procedures, not as duplicate versions of one estimate. The sponsor's reported method is rank-based, while the recalculation compares group means using the posted summary statistics.

The record does not give the sponsor's effect estimate or confidence interval for the primary analysis, so its magnitude cannot be compared directly with the recalculated mean difference. The recalculated interval is not the confidence interval for the sponsor's Wilcoxon (Mann-Whitney) result. The two p-values are close but are not interchangeable; each is tied to its own method and assumptions.

For secondary outcomes, the sponsor reports Wilcoxon (Mann-Whitney) p-values, while the posted recalculations estimate unadjusted mean differences from group summaries. Differences between p-values can arise because these methods summarize evidence differently. The registry record does not report enough detail about analysis populations, missing data, or crossover handling to resolve possible methodological differences beyond that distinction.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 39 outcome measures and 27 analyses, with 38 secondary outcomes posted. Testing or estimating many outcomes creates a multiplicity concern: when many comparisons are considered, some may appear statistically noteworthy by chance even if there is no underlying effect. General explanation: a prespecified primary endpoint, a hierarchy of outcomes, or an adjustment for multiple testing can help control how strongly a collection of findings is interpreted. The registry record does not report whether such procedures were planned or used.

Without a reported multiplicity strategy, unadjusted p-values for secondary outcomes should not be treated as if each were the only comparison in the study. This does not make the results unusable, but it lowers the confidence that an isolated secondary finding represents a reproducible signal. The primary outcome remains the central planned question as identified in the record, although the record does not provide the original protocol or statistical analysis plan needed to verify the full prespecification.

Missing-data handling is also not reported in the registry record. The summaries do not explain how many randomized participants contributed to each outcome, whether follow-up measurements were missing, or how missing observations were handled. No imputation method, sensitivity analysis, or complete-case definition is reported. If outcome availability differed between groups or follow-up times, the observed summaries might not represent all randomized participants in the same way; the available information cannot determine whether this occurred.

Analysis populations are not reported in the registry record. The record does not specify whether the primary analysis used all randomized participants, only participants with observed measurements, or another defined group. The crossover classification adds another unreported issue: treatment sequence, period effects, within-participant comparisons, and the treatment of incomplete crossover participation are not described. These gaps limit assessment of whether the posted analysis preserves the advantages of randomization and appropriately accounts for the design.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: perioperative cardiac event (takotsubo syndrome) (9.1%).

The registry reports serious adverse events among 0 of 10 participants at risk in the placebo group and 1 of 11 participants at risk in the botulinum toxin type A group. The listed serious event term is Perioperative Cardiac Event (Takotsubo syndrome), reported as 9.1%. The record also reports other adverse events affecting 3 of 10 participants at risk in the placebo group and 5 of 11 participants at risk in the botulinum toxin type A group.

These are small group counts, so they provide limited precision about the frequency of uncommon events. The figures describe events recorded during the study; they do not by themselves establish that an event was caused by the assigned treatment. The registry does not report deaths in the available safety fields, so death information is not reported in the registry record. Details such as event timing, severity grading beyond serious-event status, and attribution are not provided in the registry record for this explanation.

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

The primary result describes a difference in the recorded change in maximum capacity at cystoscopy between the botulinum toxin type A and placebo groups. The recalculated mean difference is positive, and its 95% confidence interval excludes zero. The sponsor's reported rank-based analysis also reports a p-value below 0.05. Together, these are statistical findings about the measured primary outcome in this trial; they are not a complete account of the treatment's effects or a guarantee that the same result would be observed in another study.

The result does not establish that participants experienced fewer incontinence episodes, improved quality of life, or a benefit they would notice in daily life. Those are distinct outcomes. The secondary episode results require caution because the direction of the change score is not defined clearly enough in the record to interpret positive values as favorable or unfavorable. The record also does not report a clinically important threshold for a change in maximum capacity.

The result does not prove that botulinum toxin type A caused the observed difference. Randomization and masking are design features intended to support a fair comparison, but interpretation also depends on how the crossover design was conducted and analyzed, how missing data were handled, and whether the analysis followed a prespecified plan. Those details are not reported in the registry record. The relatively small enrollment and the width of the confidence interval also leave uncertainty about the magnitude of the comparison.

Safety counts should likewise be read descriptively. The serious adverse event and other adverse event figures are observations in small groups, not precise estimates of risk or proof of causal attribution. In short, the registry reports a positive statistical comparison for the primary capacity-change outcome, alongside incomplete information about clinical meaning, design implementation, and analysis details. It should not be interpreted as a broad conclusion about all outcomes or all people with urinary urge incontinence.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result needs more than a p-value. The primary outcome is expressed on a meaningful measurement scale, and the recalculated comparison includes an estimated mean difference and confidence interval. The interval conveys that the data are compatible with a range of effect magnitudes, even though it excludes zero under the unadjusted calculation. That distinction between evidence for a difference and precision about its size is central to statistical interpretation.

The record also makes the choice of analysis visible. The sponsor reports a Wilcoxon (Mann-Whitney) analysis, while the posted recalculation uses group means and standard deviations. Rank-based and mean-based analyses answer related but distinct questions. Considering the estimate and interval alongside the sponsor's reported test helps avoid treating a single p-value as a complete result.

The crossover designation raises an important design-and-analysis question. Crossover studies can use within-participant information, but the registry record does not describe sequences, periods, washout, or how that structure was handled. The contrast between the study's design label and the limited analysis details shows why outcome summaries alone cannot establish whether a design was fully represented in the analysis.

Finally, the registry lists many outcomes and analyses, while multiplicity handling and missing-data methods are not reported. These omissions matter when interpreting secondary results and judging how robust the evidence may be. The trial is statistically instructive because it combines a numerically positive primary comparison with limited precision and incomplete information needed to assess the analysis in full.

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 reported enrollment is 21, and the primary group summaries are based on 10 for placebo and 11 for botulinum toxin type A. These small group summaries limit the precision of estimates and make the results more sensitive to individual observations. The primary confidence interval spans a broad range of possible mean differences, so the estimated magnitude should not be treated as settled.

The registry labels the design as crossover, but it does not report treatment sequence, period timing, washout, participant completion of both treatment conditions, or the analysis used to account for repeated observations within participants. The posted group summaries and reported Wilcoxon (Mann-Whitney) analysis do not resolve these questions. This is a design-specific limitation because treatment, period, and within-participant structure can be important in crossover analyses.

Missing-data methods and analysis populations are not reported in the registry record. It is therefore unclear how much outcome data were available at each follow-up and how incomplete observations were handled. The original statistical plan, sample-size justification, and any interim analysis plan are also not reported. The planning illustrations based on observed effects do not substitute for the trial's original design rationale.

Many outcome measures and analyses are listed, but a multiplicity strategy is not reported. The secondary results should consequently be interpreted cautiously. In addition, the direction and clinical meaning of episode change scores are not sufficiently defined in the record, and no clinically important threshold for the primary capacity outcome is given. These limitations prevent a complete assessment of clinical relevance, robustness, and generalizability from the posted summaries alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy of Botulinum Toxin Type A for the Treatment of Non-neurogenic Urinary Urge Incontinence — NCT01226706.
• Registry record last updated 2017-07-03; status last verified 2017-04.
• Results first posted 2017-07-03.
• 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 a completed, randomized, double-blind crossover trial of botulinum toxin type A versus placebo for non-neurogenic urinary urge incontinence. The intervention was 100U injected into the detrusor at Day 1, and the primary outcome was change in maximum capacity at cystoscopy from baseline to 6 months.

The posted primary summaries show mean changes of -97.5 mL for placebo and 64.1 mL for botulinum toxin type A. The recalculated unadjusted mean difference is 161.6 mL, with a 95% confidence interval from 35.56 to 287.6 mL; the sponsor reports a Wilcoxon (Mann-Whitney) p-value of .016. Interpretation remains limited by small group summaries and missing details about crossover analysis, missing data, multiplicity, and clinical importance.