Study to Compare the Safety and Efficacy of Solifenacin With Oxybutynin for the Treatment of Overactive Bladder (VECTOR): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Compare the Safety and Efficacy of Solifenacin With Oxybutynin for the Treatment of Overactive Bladder (VECTOR) (NCT00431041), a randomized phase 4 study. The primary outcome is The Number of Subjects Reporting Incidence of Dry Mouth as an Adverse Event.

2. Clinical Question

The registry record also lists changes from baseline in micturition frequency and urgency episodes, each reported in a subject 3-day diary, as secondary outcomes. Numerical results for those outcomes are not reported in the registry record. The primary comparison therefore addresses a specific tolerability outcome, not the full range of possible benefits and harms or every aspect of overactive bladder symptoms.

3. Trial Design

VECTOR is a completed, randomized, parallel-group phase 4 study comparing solifenacin with oxybutynin immediate release in people with overactive bladder. The registry lists enrollment as 132. The primary completion date is 2008-02, and the study start is recorded as 2006-12. The sponsor is Astellas Pharma Inc.

The intervention descriptions specify solifenacin succinate 5 mg orally once daily and oxybutynin immediate release 5 mg orally 3 times a day. The registry record lists triple masking. The official title describes the study as double-blind, while the registry masking field says triple; the record does not explain that difference. It also does not identify which roles were masked.

The parallel design assigns participants to one of the two treatment groups, with each group followed for the comparison. The primary endpoint is the number of participants in the intention-to-treat population who reported dry mouth as an adverse event over 8 weeks. The record says that dry mouth was assessed through direct questioning at each patient follow-up visit. It does not give the timing of individual visits or further details about the questioning procedure.

The registry identifies two secondary outcomes: change from baseline in micturition frequency and change from baseline in urgency episodes, both assessed using a subject 3-day diary. It lists 4 outcome measures and 2 analyses, but further details of the analyses are not reported in the registry record. Eligibility criteria, baseline characteristics, treatment adherence, and the original statistical design assumptions 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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Data represents ITT Population: all randomized subjects

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 The Number of Subjects Reporting Incidence of Dry Mouth as an Adverse Event, measured over 8 weeks.

The primary endpoint is the number of participants reporting dry mouth as an adverse event during 8 weeks. The description says that participants were asked directly about the event at each patient follow-up visit. The registry identifies the analyzed population as the intention-to-treat population, defined in the record as all randomized subjects.

This endpoint records whether a participant reported the event; it does not quantify how severe or persistent dry mouth was. Counting participants with an event gives a binary outcome for each participant: an event was reported or it was not. Such outcomes can be compared between randomized groups using counts, event proportions, and measures of difference or relative association.

Dry mouth is treated in this record as an adverse event, making the endpoint relevant to the safety comparison. It is distinct from the listed symptom outcomes of micturition frequency and urgency episodes. Those secondary outcomes are described as changes from baseline measured with a subject 3-day diary, but numerical results for them are not reported in the registry record. The primary endpoint therefore speaks to reported dry mouth within the stated follow-up, not to overall safety, symptom improvement, or outcomes beyond the recorded assessment period.

7. Results Posted in the Registry

• Oxybutynin IR: 82.8% (53/64) versus 35.3% (24/68) on control; risk difference 47.5 percentage points (95% CI 32.9 to 62.2), risk ratio 2.35 (1.67–3.30); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

For the primary endpoint, each participant contributes an event status: dry mouth was reported or was not reported. The registry’s outcome is a count of participants with an event, and the comparison is between two parallel randomized groups. This kind of endpoint is commonly described as binary. The registry identifies the analysis population as intention to treat, meaning that the outcome population is described as all randomized subjects.

What does the reported chi-squared analysis test?

The registry reports a chi-squared analysis comparing the two groups and gives p < 0.001. In general, a chi-squared test evaluates whether observed counts across categories are compatible with a model in which the groups have the same event distribution. For this endpoint, the categories are participants who reported dry mouth and participants who did not. The test summarizes evidence against equal event patterns under its assumptions; it does not estimate the size of the difference by itself.

The registry does not report a chi-squared statistic, degrees of freedom, or a test-specific confidence interval. It also does not describe any covariate adjustment. Those details are not reported in the registry record. The p-value should consequently be read as the reported result of the sponsor’s stated test, rather than as evidence that all possible sources of bias or uncertainty have been addressed.

What does the risk difference express?

The unadjusted re-calculation reports a risk difference of 0.475 for oxybutynin IR relative to solifenacin, with a 95% confidence interval from 0.329 to 0.622. A risk difference is an absolute contrast between the event probabilities in the two groups. It retains the outcome’s probability scale and gives a direct measure of how far apart the group event proportions are in the posted data. The sign and comparison direction matter: the contrast is calculated as oxybutynin IR relative to solifenacin.

The confidence interval describes a range of values compatible with the data and the calculation procedure at the stated confidence level. In general, it represents uncertainty in the estimated group contrast, not a range containing a fixed percentage of individual participant outcomes. The calculation is unadjusted and is based on the posted summary counts, rather than an individual-participant model or an adjustment for baseline characteristics.

Why are relative measures also reported?

The posted comparison gives a risk ratio of 2.346, with a 95% confidence interval from 1.669 to 3.299, and an odds ratio of 8.833, with a 95% confidence interval from 3.898 to 20.02. A risk ratio compares the probabilities of the event in the two groups. An odds ratio compares odds, where odds represent the event probability relative to the probability of no event. Because probability and odds are different scales, the odds ratio can differ notably in numerical size from the risk ratio when events are common. General interpretation should therefore identify the measure before discussing its value.

These relative measures complement, rather than replace, the absolute risk difference. Relative measures can express how event occurrence compares proportionally, while an absolute difference describes the separation in event probabilities. The measure that is most useful depends on the question; no single one gives a complete description of an outcome.

How should the two p-values be read?

The sponsor’s analysis reports p < 0.001, while the unadjusted re-calculation reports p <0.001. A p-value is a measure of how surprising data at least as extreme as those observed would be under a specified null model and test assumptions. It is not the probability that a treatment effect is absent, and it is not a measure of effect size. A small p-value does not describe the range of plausible effect sizes; the confidence interval is more informative for that purpose.

The re-calculation is a simple unadjusted analysis based on the posted summary statistics. It does not replace the sponsor’s reported analysis. The registry record identifies the sponsor method as chi-squared and does not provide enough detail to reconcile the difference in the displayed p-value thresholds. Because the discrepancy flag is false, the sponsor’s result remains the primary reported analysis, with the re-calculation serving as a separate descriptive check.

All of these methods address the recorded dry-mouth endpoint and the groups as analyzed. They cannot answer questions the record does not document, such as whether missing outcomes were handled in a particular way, whether there were prespecified subgroup analyses, or whether additional adjustment was planned. Those details are not reported in the registry record.

10. Confidence Intervals and Precision

The 95% confidence interval for the unadjusted risk difference is 0.329 to 0.622. It is centered around an estimated difference of 0.475, but the interval is more informative than the point estimate alone because it displays uncertainty compatible with the posted counts and the calculation method. The entire interval is above zero, which is consistent with the observed direction of the contrast: more reported dry-mouth events in the oxybutynin IR group than in the solifenacin group.

In general, a confidence interval describes the range of effect values that are reasonably compatible with the data under the method used. It does not mean there is a 95% probability that the particular interval contains the true effect. Nor does it capture every source of uncertainty. It does not automatically account for measurement differences, missing outcomes, selection effects, or choices made in the trial’s design and analysis.

The posted relative estimates also have intervals: the risk ratio is 2.346, with a 95% confidence interval from 1.669 to 3.299, and the odds ratio is 8.833, with a 95% confidence interval from 3.898 to 20.02. These intervals belong to different measures and should be interpreted on their corresponding scales. Their widths convey uncertainty about each relative estimate, not about the risk difference.

The event counts are finite, and the registry reports no interval alongside the raw counts. The re-calculated intervals are based on the posted summary statistics and are unadjusted. Details of the interval construction are not reported in the registry record. Precision should therefore be considered together with the analysis population, the endpoint’s assessment method, and the limited information available about missing data and other analyses.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect, not the trial’s original design calculation. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect.

For planning for 100% of the observed effect, the illustration gives 16 participants per arm for 80% power and 21 participants per arm for 90% power. For planning for 75% of the observed effect, it gives 30 participants per arm for 80% power and 40 participants per arm for 90% power. For planning for 50% of the observed effect, it gives 69 participants per arm for 80% power and 91 participants per arm for 90% power.

In general, power is the chance that a study will detect an effect of a specified size under the assumed model and testing procedure. The 80% power column gives the illustrative group size associated with an 80% chance of detecting the scenario’s stated effect; the 90% power column gives the corresponding size for a 90% chance. The figures are planning illustrations, not observed power. Smaller effects require more participants under these assumptions, as reflected by the increasing planning figures across the displayed effect scenarios.

The original sample-size justification and design assumptions are not reported in the registry record. The planning values should not be taken as evidence that the completed study was designed using these assumptions.

12. 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.353; treatment proportion p₁ = 0.828; average p̄ = 0.591.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6954 = 1.3630.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6089 = 0.5124.
4. n = (1.3630 + 0.5124)² / (0.4752)² = 15.6, rounded up to 16 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
p0 <- 0.352941176470588                          # control proportion
p1 <- 0.828125                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(431041)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 16 (80% power), 21 (90% power)
 75% of observed effect: n per arm = 30 (80% power), 40 (90% power)
 50% of observed effect: n per arm = 69 (80% power), 91 (90% power)
power.prop.test: 15.6 
Simulated power at n = 16 per arm: 0.823 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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.

13. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison as a chi-squared analysis, with p < 0.001. That is the trial’s own reported analysis and takes precedence over the separate unadjusted re-calculation. The re-calculation uses the posted summary counts to estimate a risk difference of 0.475, with a 95% confidence interval from 0.329 to 0.622, and reports p <0.001.

The two p-values are not identical, though both are reported as less-than thresholds. The registry record does not give enough detail to explain the difference, such as the exact computational choices behind each result. The discrepancy flag is false, so the figures are presented as distinct analyses rather than as a documented correction to the sponsor’s result.

The sponsor’s p-value addresses the test of the group comparison, while the re-calculation adds unadjusted effect estimates and confidence intervals derived from the posted counts. Neither should be interpreted as the probability that a treatment is effective or ineffective. The sponsor’s reported result is the primary record of the trial’s analysis; the re-calculated estimates offer a transparent, summary-data-based view of the magnitude and precision of the contrast.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome of dry mouth incidence and two secondary outcomes: change from baseline in micturition frequency and change from baseline in urgency episodes, both measured using a subject 3-day diary. It also lists 4 outcome measures and 2 analyses. Numerical results for the diary outcomes are not reported in the registry record.

When a study evaluates several outcomes or conducts several statistical tests, the chance of at least one apparently unusual result can increase. General methods for addressing this include prespecifying a primary outcome, adjusting significance thresholds, or using a structured testing sequence. The registry record does not report whether multiplicity was considered, whether any adjustment was used, or how the listed analyses relate to the outcome measures. Those details are not reported in the registry record, so no conclusion can be drawn about the trial’s multiplicity strategy.

The primary outcome description identifies the intention-to-treat population as all randomized subjects. This clarifies the population label, but it does not specify how missing dry-mouth assessments were handled, whether all randomized participants contributed endpoint data, or how any deviations from assigned treatment were treated in the analysis. These details are not reported in the registry record.

Likewise, the record does not describe a missing-data method, imputation, sensitivity analysis, subgroup analysis, interim analysis, or adjustment for baseline variables. Their absence from the available record does not establish that such procedures were or were not used; it means they are not reported in the registry record. The posted result can be interpreted as the reported comparison for the defined primary outcome, but the reader cannot assess these unreported analysis choices from the record alone.

15. 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 4.5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: fracture, right foot (1.5%), cervical adenocarcinoma in situ (1.5%), worsening depression (1.5%).

The registry lists serious adverse events affecting 3 of 68 participants in the solifenacin group and 0 of 64 participants in the oxybutynin IR group. It separately lists other adverse events affecting 36 of 68 participants in the solifenacin group and 56 of 64 participants in the oxybutynin IR group. These are the registry’s event counts and denominators; serious and other adverse events are separate categories in the record.

The listed serious adverse event terms are fracture, right foot; cervical adenocarcinoma in situ; and worsening depression, each shown with a frequency of 1.5%. The record does not identify the treatment group for each listed term in the registry record for this comparison, so they should not be assigned to a particular group. Death counts are not reported in the registry record.

Serious adverse event counts should not be treated as a complete safety comparison. They do not, by themselves, describe severity beyond the serious classification, timing, duration, relatedness to treatment, or clinical consequences. The registry record’s endpoint specifically concerns dry mouth over 8 weeks, while the broader adverse-event counts are listed separately. They should be read as descriptive record entries, not as proof of causation or as a comprehensive account of safety.

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

The posted primary endpoint results show that dry mouth was reported by 24 of 68 participants assigned to solifenacin and 53 of 64 participants assigned to oxybutynin IR during the 8-week assessment period. The unadjusted risk difference is 0.475, with a 95% confidence interval from 0.329 to 0.622. The registry’s sponsor-reported chi-squared analysis gives p < 0.001. Together, these statistics describe a marked difference in reported dry-mouth incidence between the groups in this trial.

The result is specific to dry mouth as recorded through direct questioning at follow-up visits. It does not measure intensity, duration, impact on daily activities, or whether a participant stopped treatment. It does not establish how the groups compare on the secondary diary outcomes, since numerical results for those measures are not reported in the registry record. Nor does this single endpoint summarize all benefits and harms.

The randomized design supports a comparison between the assigned groups, but interpretation still depends on how outcomes were collected and analyzed. Details about missing assessments, adherence, participant characteristics, and any additional statistical adjustments are not reported in the registry record. The study’s 8-week timeframe also limits the result to the recorded follow-up period.

Statistical evidence and clinical importance are different questions. The p-value describes compatibility with a no-difference model under the stated test; it does not determine whether the observed contrast is important to patients or how it should affect care. The findings describe what the registry reports for these groups and this endpoint. They do not establish a universal effect in every population or answer treatment decisions for an individual.

17. Why This Trial Matters Statistically

This trial illustrates why an event count, an effect estimate, and a test result should be read together. The counts show how many participants in each group reported dry mouth. The risk difference expresses the absolute separation in event probability, while the risk ratio and odds ratio express relative comparisons on different scales. The confidence intervals add information about precision that a p-value alone does not provide.

It also illustrates the importance of distinguishing a registry-reported analysis from an unadjusted re-calculation. The sponsor’s chi-squared result is the trial’s own reported analysis. The re-calculated estimate uses the posted summary counts and provides an effect size and interval, but it is not a substitute for a fuller analysis based on participant-level information or details of the trial’s prespecified plan.

Finally, this record highlights the boundary between a focused endpoint and a broad conclusion. Dry mouth is a specific adverse-event outcome assessed during 8 weeks. Other symptom outcomes are listed, but their numerical results are not reported in the registry record. Serious and other adverse-event counts add descriptive safety information, yet do not settle questions about severity, attribution, or longer-term outcomes. Keeping these distinctions clear helps prevent a single test or endpoint from being asked to answer more than it can.

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.

The primary result concerns dry mouth assessed by direct questioning at follow-up visits. The registry does not report the exact wording of the questions, how an event was defined, or how severity and duration were recorded. Those missing details limit assessment of the measurement process. The endpoint counts whether a participant reported the event; it does not describe its intensity or consequences.

The stated follow-up for the primary endpoint is 8 weeks. The record therefore does not describe longer-term event patterns. The registry record also does not report the schedule of follow-up visits, participant adherence, treatment discontinuation, or whether participants received other relevant care during follow-up.

The outcome description specifies an intention-to-treat population of all randomized subjects, but the registry does not explain how missing assessments were handled or whether all participants had evaluable endpoint information. Baseline characteristics and eligibility details are not reported in the registry record, limiting assessment of how the enrolled group compares with other patient populations.

Numerical results for the listed diary outcomes are not reported in the registry record. The available primary result therefore cannot establish the pattern of effects across the full set of recorded outcomes. Further, the record does not report the original sample-size justification, detailed statistical plan, multiplicity handling, subgroup analyses, or interim analyses. The interpretation of the primary comparison should remain tied to the posted result and these limitations, rather than being extended to unreported outcomes or analysis choices.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study to Compare the Safety and Efficacy of Solifenacin With Oxybutynin for the Treatment of Overactive Bladder (VECTOR) — NCT00431041.
• Registry record last updated 2010-06-08; status last verified 2010-06.
• Results first posted 2010-01-11.
• 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

NCT00431041, titled VECTOR, is a completed, randomized, parallel-group phase 4 study sponsored by Astellas Pharma Inc. The registry records a study start of 2006-12, primary completion in 2008-02, and enrollment of 132. It compares oral solifenacin succinate 5 mg once daily with oral oxybutynin immediate release 5 mg 3 times a day.

The primary endpoint is the number of participants reporting dry mouth as an adverse event over 8 weeks, assessed by direct questioning at follow-up visits. The intention-to-treat population is described as all randomized subjects. The sponsor’s reported analysis is chi-squared, with p < 0.001. The posted counts are 24 of 68 for solifenacin and 53 of 64 for oxybutynin IR. The unadjusted risk difference is 0.475, with a 95% confidence interval from 0.329 to 0.622.

Two diary-based secondary outcomes are listed, but their numerical results are not reported in the registry record. The record also does not describe several design and analysis details relevant to broader interpretation.