Overactive Bladder Innovative Therapy Trial (OrBIT): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Overactive Bladder Innovative Therapy Trial (OrBIT) (NCT00448175), a randomized phase 4 study. The primary outcome is Frequency of Voids at 12 Weeks.

2. Clinical Question

This is a comparison of two treatment strategies in a randomized, parallel-group trial. The central statistical issue is not only which arm had the larger average change, but also how precisely the between-arm difference was estimated. The registry reports an average change for each arm and an interval for their mean difference. Those results can describe the observed changes and the uncertainty around the comparison, but they do not by themselves establish equivalence or noninferiority. Such conclusions require an appropriate prespecified margin and an analysis that evaluates the estimate against that margin; those details are not reported in the registry record.

3. Trial Design

The Overactive Bladder Innovative Therapy Trial, also identified as OrBIT, was a Phase 4 randomized, parallel-group study. Its stated condition was overactive bladder. The registry lists an overall enrollment of 100 and a completed status. The study began in June 2006, with primary completion in October 2008. Uroplasty, Inc was the sponsor.

The two treatments were the Urgent PC Neuromodulation System and 4mg Daily Tolterodine. The study summary describes the first as percutaneous tibial nerve stimulation and says the purpose was to compare it with drug therapy for overactive bladder symptoms. The registry identifies the intervention type for Urgent PC as a device and the type for tolterodine as a drug. The design is listed as randomized and parallel, with no masking. That means the record describes participants as assigned across concurrent groups, but does not describe blinding of participants or other parties.

The primary outcome was frequency of voids at 12 weeks, expressed in voids per day. Its stated timeframe was baseline to 12 weeks, and the outcome description says that voiding diaries at 12 weeks were compared with baseline diaries. The reported arm counts for this outcome were 41 for Urgent PC and 43 for tolterodine. The overall enrollment and these outcome-specific counts describe different quantities; the record does not explain the difference between them.

Four secondary outcomes are listed: urge incontinence episodes, volume voided, OAB quality of life, and known side effects, each through 12 weeks or at 12 weeks as named in the record. Although the record lists five outcome measures in total, it reports no posted analyses. The protocol details, eligibility criteria, allocation procedures, masking procedures beyond the listed absence of masking, and the trial’s original sample-size justification are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: After 12 weekly PTNS treatments, 35 patients were considered responders (reporting of "Moderately" or "Markedly" improved on the Global Response Assessment (GRA))and allowed to continue in the trial through 12 months.

12 Weeks PTNS vs. Drug

Continued PTNS Through 12 Months

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 Frequency of Voids at 12 Weeks, measured over Baseline to 12 weeks.

The primary endpoint measures the change in the number of urinary voids per day from baseline to 12 weeks. The unit is voids per day, and the registry identifies the summary measure as a mean with standard deviation. The endpoint description says the assessment used voiding diaries completed at baseline and at 12 weeks. It is therefore a continuous outcome: each participant’s diary contributes a numerical frequency, and the arm-level result summarizes the average change.

Measuring change over a specified period makes the outcome relevant to the trial’s stated comparison of treatments for overactive bladder symptoms. Comparing mean changes between randomized groups provides an estimate of the average difference in change during the follow-up period. The reported arm means are -2.4 for Urgent PC and -2.5 for tolterodine. These are changes in daily void frequency, not the final number of voids per day. Baseline and follow-up values themselves are not reported in the registry record.

The endpoint was selected to address the study’s stated question about voiding frequency. However, a mean describes the average and does not show how changes varied among participants or how many experienced a particular degree of change. The record also does not report the diary completion rules, handling of incomplete diaries, or any threshold for a clinically meaningful change. The outcome can therefore be interpreted as a group-level measure of average change, with its uncertainty considered alongside the estimate.

7. Results Posted in the Registry

• 4mg Daily Tolterodine: mean -2.50 versus -2.40 on control; difference -0.10 (95% CI -1.79 to 1.59), standardized effect d = -0.03; z-test p = 0.908.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a mean change describe?

The primary outcome is continuous, meaning it is measured on a numerical scale. For each arm, the registry reports the mean change in voids per day and a standard deviation. The mean gives the average change across participants with reported outcomes. The standard deviation describes the spread of individual observations around that average. It is not the uncertainty in the mean itself: uncertainty in an estimated mean also depends on the number of observations and the variability among them.

The reported changes are -2.4 for Urgent PC and -2.5 for tolterodine. Negative changes indicate a reduction in the measured daily frequency relative to baseline, according to the stated change outcome. The comparison focuses on the difference between the two arm means rather than treating either arm’s change in isolation. A within-arm change alone does not tell whether the change differs from what would have occurred under the other treatment.

What does the between-arm estimate represent?

The registry reports a mean difference of -0.1 for the tolterodine comparison, with an interval from -1.791 to 1.591. This is the estimated contrast between the arm-level mean changes. A contrast puts the two groups on a common scale and expresses the estimated separation between their average changes. The reported interval conveys uncertainty about that separation. Its inclusion of values on either side of zero means that the estimate does not precisely determine the direction of a possible difference.

The registry also reports a pooled standard deviation of 3.949 and a standardized effect estimate of -0.025. A standardized effect expresses a difference relative to variability, which can help describe its scale without using the original measurement unit. Such a standardized value does not replace the original-unit estimate: voids per day is the direct scale for understanding the primary outcome. These quantities remain summaries of the posted data, not proof that a difference is absent.

What does the p-value tell the reader?

The unadjusted p-value is 0.908. In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test assumptions held. It is not the probability that the null is true, and it is not a measure of clinical importance. The record labels this value unadjusted; it does not report a multiplicity-adjusted p-value or a detailed description of the test used. A high p-value does not establish equivalence or noninferiority.

The posted sample-size planning assumptions use a two-sided significance level of 0.05. That assumption belongs to a planning illustration based on the observed effect; it does not establish the analysis plan used for the original trial. The original statistical plan and any prespecified hypothesis-testing details are not reported in the registry record.

Why does variability matter?

When participant outcomes vary substantially, the arm mean may be estimated less precisely than when outcomes are more closely grouped, all else being equal. The standard deviations of 4.0 and 3.9 are relatively large compared with the mean difference of -0.1. This helps explain why a small point estimate can coexist with an interval that spans a wider range of possible differences. The posted interval, rather than the point estimate alone, is important for judging precision.

General statistical note: over-dispersion refers to variability greater than a model expects. In a count outcome, for example, a simple model may assume that variability follows a specified relationship to the mean. If the actual observations are more variable, uncertainty can be understated unless the model accounts for that extra variability. The registry record does not identify a count-data model or report an analysis of over-dispersion. The primary outcome is reported as a mean change with a standard deviation, so the displayed comparison should be understood using the summary statistics actually posted rather than assuming a particular model.

How does noninferiority differ from a test for any difference?

A conventional two-sided comparison asks whether the data provide evidence of a difference in either direction. A noninferiority analysis asks whether the intervention is not worse than the comparator by more than a prespecified acceptable margin. The margin must be stated to interpret that question. A confidence interval can be compared with the margin, but the relevant direction and analysis must also be specified. Here, the study description names noninferiority as an objective, but the margin and formal noninferiority analysis are not reported in the registry record. Therefore, the ordinary reported comparison cannot be treated as a noninferiority finding.

Randomization can support a fair comparison by reducing systematic differences in treatment assignment, but interpretation still depends on how participants were analyzed, the amount and handling of missing data, and whether the analysis followed a prespecified plan. The registry record does not report those details. No adjusted analysis or additional analysis is posted.

10. Confidence Intervals and Precision

The mean difference is reported as -0.1 voids per day, with an interval from -1.791 to 1.591. The point estimate is the single best estimate in the reported comparison, while the interval expresses uncertainty around it. The interval covers negative and positive values, so the results do not establish a precise direction for the difference. The registry does not state the confidence level attached to the interval, so no confidence percentage is assigned.

Precision concerns how narrowly the data locate an effect, not whether the effect is important. The interval spans values that would represent differences in either direction, including values farther from zero than the point estimate. Thus, the small estimated difference should not be read as showing that any true difference must also be small. The sample sizes for the primary outcome were 41 for Urgent PC and 43 for tolterodine, and the reported standard deviations were 4.0 and 3.9. These features help place the interval in context, but the interval is the direct summary of uncertainty for the contrast.

The interval also cannot be used to declare noninferiority without the noninferiority margin. For that purpose, the relevant question is whether the interval rules out an unacceptable loss specified in advance, not merely whether it includes zero. The margin and the corresponding formal analysis are not reported in the registry record. The reported interval therefore describes uncertainty in the mean difference but does not, on its own, resolve the study’s stated noninferiority objective.

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 for 80% power and participants per arm for 90% power. They are planning illustrations based on the observed effect, not counts of participants in the trial. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. These assumptions describe the planning calculation; the original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned number of participants in each arm under the stated assumptions for a design with 80% probability of detecting the specified effect if that effect were the true one and the assumptions held. The 90% column describes the corresponding planning target for 90% probability. Higher planned power generally requires more participants when other assumptions are held fixed. These are prospective design illustrations, not an estimate of how likely the completed trial was to produce a significant result.

The displayed planning scenarios use 100%, 75%, and 50% of the observed effect. Smaller effects need more participants to detect under the same assumptions. The reported per-arm requirements are 24,482 and 32,774 for planning around 100% of the observed effect; 43,523 and 58,264 for planning around 75%; and 97,925 and 131,094 for planning around 50%, for 80% and 90% power respectively. The observed effect is very small, so these planning requirements are very large. This is not observed power.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.100; pooled standard deviation σ = 3.949.
2. n = 2 × (1.96 + 0.842)² × 3.949² / -0.100² = 24,481.2, rounded up to 24,482 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 <- -0.1                      # observed difference in means
sigma <- 3.94909684024823                     # 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(448175)
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 = 24,482 (80% power), 32,774 (90% power)
 75% of observed effect: n per arm = 43,523 (80% power), 58,264 (90% power)
 50% of observed effect: n per arm = 97,925 (80% power), 131,094 (90% power)
power.t.test: 24482.2 
Simulated power at n = 24,482 per arm: 0.797 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists five outcome measures in total: the primary outcome and four secondary outcomes. The secondary outcomes are urge incontinence episodes at 12 weeks, volume voided at 12 weeks, OAB quality of life at 12 weeks, and known side effects through 12 weeks. However, the record reports zero posted analyses. The primary comparison is available, but the secondary outcomes do not have posted analysis results in the registry record.

Multiplicity arises when several outcomes or statistical tests are considered. In general, conducting multiple tests can increase the chance that at least one result appears statistically notable by chance. Researchers may address this with a prespecified hierarchy, adjusted significance thresholds, or other methods. The registry record does not report a multiplicity strategy, a testing hierarchy, or an adjusted analysis. The posted p-value is described as unadjusted, so it should not be interpreted as a multiplicity-controlled result.

The record also does not report how missing primary outcome data were handled, whether any participants were excluded from an analysis, or whether the analysis followed an intention-to-treat or per-protocol approach. The primary outcome counts are 41 and 43, while overall enrollment is 100. The record does not explain this difference, so its causes cannot be determined from the posted information. It does not provide completion rates by arm or identify the number of participants with missing diaries.

These omissions matter because missing outcomes and analysis-population choices can affect the interpretation of treatment comparisons. In a noninferiority setting, in particular, the choice of analysis population and the handling of missing data can be important to evaluating the result. The protocol, statistical analysis plan, imputation method, and sensitivity analyses are not reported in the registry record. The available summary therefore supports interpretation of the posted estimates but not a full audit of the analysis choices.

14. 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 non-serious adverse event terms

The serious adverse event counts are reported as 0 of 50 participants at risk in the Urgent PC group and 0 of 50 at risk in the tolterodine group. These are the serious-event figures recorded for the groups; the registry lists no serious adverse event terms. The record does not report deaths for either group, so death counts are not reported in the registry record.

The adverse-event information also reports other adverse events affecting 6 of 50 participants in the Urgent PC group and 4 of 50 in the tolterodine group. These are counts of participants affected as recorded, not a comparison adjusted for differences in exposure or other factors. The record does not give event-level detail for these other adverse events in the registry record.

Zero recorded serious events in both groups does not prove that serious events cannot occur, nor does it establish that the treatments have identical safety profiles. Safety interpretation depends on the duration and completeness of follow-up, how events were defined and collected, and the amount of information available. Details such as event definitions, severity classifications beyond the serious-event category, and follow-up completeness are not reported in the registry record. The counts should be read as the posted observations, not as a definitive safety comparison.

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

The primary result is a comparison of average change in daily void frequency over 12 weeks. The mean changes were -2.4 with Urgent PC and -2.5 with 4mg Daily Tolterodine. The reported between-arm mean difference was -0.1, with an interval from -1.791 to 1.591 and an unadjusted p-value of 0.908. These statistics describe a small observed difference, but the interval shows that the estimate is not precise enough to restrict the possible difference to values close to zero.

The result does not demonstrate that the treatments are equivalent. A finding of no statistically significant difference is not the same as evidence that any difference is negligible. Equivalence requires prespecified bounds defining differences considered acceptably small and an analysis that tests the comparison against those bounds. Those details are not reported in the registry record.

Nor does the result establish noninferiority, despite the objective’s wording. Noninferiority requires an explicit margin and a suitable analysis to determine whether the intervention rules out a loss greater than that margin. The margin and formal noninferiority result are not reported in the registry record. The posted mean difference and interval can be described, but they cannot substitute for those missing elements.

The reported outcome is an average change and does not show the range of individual experiences or the proportion of participants whose frequency changed by a particular amount. Baseline and final values are not reported in the registry record. The secondary outcomes are listed but have no posted analyses, so the primary result does not answer questions about urge incontinence episodes, volume voided, quality of life, or side effects beyond the adverse-event counts.

In general, trial results are most informative when interpreted with the design, analysis population, missing-data handling, and prespecified statistical plan. Several of these details are not reported in the registry record. The posted data therefore support a careful description of the observed summary comparison and its uncertainty, but not a broader claim about equivalence, noninferiority, or outcomes that were not analyzed.

16. Why This Trial Matters Statistically

This trial illustrates why a point estimate and its uncertainty should be read together. The arm-level mean changes are close, and the estimated between-arm difference is -0.1. Considered alone, that point estimate might suggest little separation in average change. The interval, however, extends from -1.791 to 1.591, allowing a substantially wider range of possible differences. Precision is therefore central to interpreting the result.

It also demonstrates a key distinction between a test for a difference and a noninferiority question. A large unadjusted p-value does not establish that two treatments are similar enough for a noninferiority claim. Such a claim requires an acceptable margin chosen in advance and an analysis that evaluates the evidence against it. The registry states that noninferiority was an aim, but does not report the margin or formal noninferiority analysis.

The planning illustration provides another statistical lesson: sample-size requirements depend strongly on the effect a study is intended to detect. The posted scenarios show much larger participant requirements as the target effect becomes a smaller fraction of the observed effect. These values are not the original trial design calculation and are not evidence about the trial’s observed power. The record’s original sample-size justification is not reported.

Finally, the difference between overall enrollment and the primary outcome counts, together with the absence of posted secondary analyses and details of missing-data handling, shows why registry summaries may not contain enough information to fully evaluate an analysis. The result remains interpretable as a reported mean comparison, but its scope is limited by what the record documents.

17. Limitations

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

The registry record does not provide a detailed participant profile, eligibility criteria, or a description of the setting. The listed condition is overactive bladder, but the population beyond that label is not described. This limits assessment of how closely the participants may resemble a particular clinical population.

There is a gap between the overall enrollment of 100 and the primary outcome counts of 41 and 43. The record does not explain whether the difference reflects missing diaries, exclusions, a distinction between enrollment and randomization, or another reason. No analysis population, participant flow, or missing-data approach is reported. These details are important for evaluating whether the group estimates could be affected by incomplete outcome data.

The primary outcome description identifies a baseline-to-12-week comparison using voiding diaries, but diary completion rules and the method used to calculate each participant’s change are not reported. Baseline values and final values are also absent. The registry does not report the confidence level for the displayed interval or provide a detailed statistical analysis plan.

The objective is described as noninferiority, but the noninferiority margin and a formal noninferiority analysis are not reported in the registry record. The absence of these details prevents the mean comparison from answering whether the stated criterion was met. Multiplicity methods are also not reported, and the four listed secondary outcomes have no posted analyses.

For safety, the record reports group counts for serious and other adverse events but does not provide event-level detail for the other adverse events in the summary. It does not report deaths. Follow-up completeness and event-collection methods are not described. These limitations call for a narrow reading of the available information: the posted summary estimates and counts, rather than a comprehensive evaluation of efficacy, noninferiority, or safety.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Overactive Bladder Innovative Therapy Trial (OrBIT) — NCT00448175.
• Registry record last updated 2013-05-16; status last verified 2013-04.
• Results first posted 2013-05-16.
• 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.

21. Record Summary

OrBIT was a completed Phase 4 randomized, parallel-group trial without masking, sponsored by Uroplasty, Inc. It enrolled 100 participants and compared the Urgent PC Neuromodulation System with 4mg Daily Tolterodine for overactive bladder. The study began in June 2006 and reached primary completion in October 2008.

The primary outcome was change in frequency of voids per day from baseline to 12 weeks. Mean changes were -2.4 for Urgent PC and -2.5 for tolterodine; the reported mean difference was -0.1, with an interval from -1.791 to 1.591 and an unadjusted p-value of 0.908. The outcome counts were 41 and 43, respectively. Four secondary outcomes are listed, but no analyses are posted. A noninferiority margin, original sample-size justification, and details of missing-data handling are not reported in the registry record.