Timing of Repeat Voiding Trials After Outpatient Pelvic Floor Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Timing of Repeat Voiding Trials After Outpatient Pelvic Floor Surgery (NCT03048682), a randomized na study. The primary outcome is Failed Office Voiding Trials.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. It was designed to compare an early repeat office voiding trial with a later repeat trial among patients who had failed an initial same-day voiding trial after outpatient pelvic floor surgery. The record lists Foley catheter interventions for both groups. Participants assigned to the early group were scheduled for an office trial on post-operative day 2, 3, or 4; those assigned to the late group were scheduled for day 7 or after, which the record identifies as current practice.

The registry reports enrollment of 64 and lists the study status as completed. The primary outcome results give a denominator of 30 in each group. The record does not explain the relationship between the enrollment figure and the outcome denominators, so it is not possible to determine from the registry record whether the difference reflects exclusions, unavailable outcome data, or another reason. Randomization procedures, allocation concealment, and the handling of participants who did not follow their assigned timing are not reported in the registry record.

The primary outcome was failed office voiding trials within 8 days of surgery. Urinary tract infections within 6 weeks of surgery were also posted as a secondary outcome. The listed secondary outcomes include catheter-related bother, but a result for that outcome is not reported in the registry record. The registry lists no reported analyses. It also does not report the trial’s original sample-size justification, a detailed statistical analysis plan, or whether any interim analyses were planned.

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 Failed Office Voiding Trials, measured over within 8 days of surgery.

The primary endpoint counts participants who experienced a failed office voiding trial within 8 days of surgery. It therefore records whether each participant had the event during the stated period, rather than how many attempts were made or how long catheter use continued. The registry does not provide a more detailed operational definition of failure, such as the criteria used at the office visit; those details are not reported in the registry record.

A binary endpoint is useful for comparing the frequency of an event between randomized groups. The posted counts are 7 participants among 30 in the early group and 1 participant among 30 in the late group. The comparison is presented as a risk difference for late versus early timing. A risk difference describes the difference between the two groups’ event probabilities on an absolute scale. In this comparison, a negative estimate corresponds to a lower observed event probability in the late group.

As a general statistical point, a clearly defined time window makes the outcome easier to interpret: events outside that window are not part of this endpoint. The time boundary also means the result does not describe longer-term voiding outcomes. The registry record does not report whether events occurring after the stated window were collected as part of another outcome.

7. Results Posted in the Registry

• Late Voiding Trial: 3.3% (1/30) versus 23.3% (7/30) on control; risk difference -20.0 percentage points (95% CI -36.4 to -3.6), risk ratio 0.14 (0.02–1.09); unadjusted two-proportion z-test p = 0.023.

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.

Urinary Tract Infections

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Late Voiding Trial: 6.7% (2/30) versus 23.3% (7/30) on control; risk difference -16.7 percentage points (95% CI -34.2 to 0.9), risk ratio 0.29 (0.06–1.26); unadjusted two-proportion z-test p = 0.071.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Late Voiding Trial and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide context but do not carry the same evidential weight as the primary endpoint. The posted urinary tract infection comparison points in the same direction as the primary comparison, with fewer observed events in the late group. Its uncertainty includes no group difference, and its reported unadjusted p-value is 0.071. The listed outcome of catheter-related bother has no result reported in the registry record, so the secondary evidence is incomplete.

As a general statistical point, secondary outcomes can help assess whether a primary pattern is accompanied by related findings, but they often involve additional comparisons. When several outcomes are examined, the chance of at least one apparently notable result can increase. This is why prespecified outcome priorities and multiplicity procedures matter. The registry record does not report a multiplicity adjustment or a statistical hierarchy that would indicate how the secondary results were intended to be interpreted.

The secondary pattern is compatible with the direction of the primary result but does not establish that the primary contrast is robust across different outcomes. The outcomes measure different events and have different time windows: urinary tract infections are reported within 6 weeks of surgery, whereas the primary endpoint covers failed trials within 8 days. Differences in outcome definition and follow-up mean the results should not be treated as interchangeable replications.

Unadjusted secondary results should therefore be read as exploratory descriptions of the posted data, not as independent proof of a treatment effect. The record does not report analyses adjusting for multiple outcomes, nor does it provide a result for catheter-related bother. The overall secondary evidence is consequently limited and should not be used to strengthen the primary conclusion beyond what its own estimate and uncertainty support.

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

• Urinary Tract Infections
• Rate of Bother From Urinary Catheter

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary comparison is a risk difference between late and early repeat-trial timing. The risk difference uses the event probability in one group minus the event probability in the other group. Here, the comparison is late versus early: the reported estimate is -0.2. A negative value indicates that the observed event probability was lower in the late group on this scale. This is an absolute contrast, not a relative measure. It does not describe the proportion of events prevented or the probability that an individual patient will have a failure.

What does a confidence interval express?

As a general statistical explanation, a confidence interval describes the range of estimates compatible with the observed data under the method’s assumptions. It conveys precision as well as direction. A narrower interval indicates greater precision, while a wider interval leaves more uncertainty about the size of the underlying contrast. For this primary comparison, the reported interval runs from -0.364 to -0.036. Because the interval is entirely below zero, the displayed interval is consistent with a lower event probability in the late group on the risk-difference scale. Its width also signals that the exact size of the contrast is not pinned down precisely.

How should the p-value be read?

As a general statistical explanation, a p-value evaluates how unusual data at least as discrepant as the observed data would be if a specified null hypothesis were true, subject to the model and test assumptions. It is not the probability that the null hypothesis is true, and it is not a measure of clinical importance. The registry reports an unadjusted p-value of 0.023 for the primary comparison. The record does not identify the test or describe all of its assumptions, so the p-value should be read as the posted unadjusted result rather than as a complete account of the analysis.

What do relative measures add?

The registry also reports relative-risk and odds-ratio summaries for the primary comparison. Such measures describe a contrast relative to the event level in the comparison group, rather than an absolute difference in event probability. They can help express the same comparison from another perspective, but they are not interchangeable with a risk difference. Their interpretation can be especially sensitive when event counts are small. The posted relative measures have broad uncertainty, and the relative-risk interval includes 1. The odds-ratio interval is reported as 0.013 to 0.988. The registry does not report a separate model-based adjustment for either measure.

As a general point, randomization is intended to balance factors between groups on average, but the registry record does not give baseline characteristics or details of the randomization process. It therefore does not allow readers to assess balance or allocation concealment from the posted information. The record lists no reported analyses and does not specify an inferential procedure, analysis population, missing-data method, or approach to participants who did not receive the assigned timing. No such procedures should be inferred from the reported estimates.

Over-dispersion is a concern mainly for count outcomes when variability exceeds what a simple count model expects. It is not the central issue for this primary endpoint, which is posted as a count of participants with a binary event. As a general statistical concept, a model that ignores excess variability can make uncertainty appear too small. The registry does not report a count model or a dispersion estimate for the primary outcome.

The methods information is therefore clearest about the outcome, group counts, estimated contrasts, and unadjusted p-value, but incomplete about the analytic procedure. A careful reading separates the reported numerical comparison from unreported design and analysis details. The endpoint counts can be described directly; conclusions about adjustment, model choice, missing outcomes, or robustness cannot be drawn from the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate for late versus early timing is -0.2, with a 95% confidence interval from -0.364 to -0.036. This interval lies below zero, so the interval-based comparison is consistent with a lower event probability in the late group. It does not identify one exact underlying difference. Values across the interval remain compatible with the posted data under the interval method’s assumptions, and the interval allows a range of possible effect sizes.

As a general statistical explanation, confidence intervals communicate precision rather than certainty about an individual outcome. An interval that excludes zero can still be broad enough to leave substantial uncertainty about the magnitude of a group difference. The primary interval extends from an appreciably negative estimate to a value nearer zero, so it supports a direction more clearly than an exact size. The registry record does not report the method used to construct the interval.

The comparison is based on 30 participants in each group and a small number of recorded failures. Limited event information can make estimates sensitive to the outcomes of a few participants. The registry reports relative-risk and odds-ratio intervals as well, but these should not be treated as independent confirmation: they are alternative summaries of the same group data. The relative-risk interval includes 1, while the odds-ratio interval is reported from 0.013 to 0.988.

Precision should also be considered alongside the outcome’s short time window. The primary endpoint concerns failures within 8 days of surgery, not later function. Uncertainty about longer-term outcomes is not represented by this interval. The registry record does not report follow-up beyond the posted outcome windows or describe how missing outcome information was handled.

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 for this binary endpoint are expressed as participants per arm, not total events. The planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is a stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 45 participants per arm for 80% power and 59 participants per arm for 90% power. Planning for 75% of the observed effect gives 92 participants per arm for 80% power and 123 participants per arm for 90% power. Planning for 50% of the observed effect gives 234 participants per arm for 80% power and 313 participants per arm for 90% power.

In plain language, the 80% and 90% columns describe the target chance of detecting the chosen effect under the stated planning assumptions if that effect were the true one. The higher target power requires a larger planned group size. The rows also illustrate that smaller effects need more participants to detect, all else held to the stated assumptions. These are planning illustrations based on the observed effect, not observed power.

The observed effect in a small trial can be unstable, so basing a future design directly on it may produce an optimistic target if the observed contrast is larger than the underlying contrast. The figures are therefore scenario-based planning aids rather than a recommendation or a description of the original trial’s design. The registry record does not report the assumptions used when the trial was originally planned.

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

Worked calculation for this trial

1. Control proportion p₀ = 0.233; treatment proportion p₁ = 0.033; average p̄ = 0.133.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4807 = 0.9422.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4595 = 0.3867.
4. n = (0.9422 + 0.3867)² / (-0.2000)² = 44.2, rounded up to 45 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 <- 0.233333333333333                          # control proportion
p1 <- 0.0333333333333333                          # 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(3048682)
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 = 45 (80% power), 59 (90% power)
 75% of observed effect: n per arm = 92 (80% power), 123 (90% power)
 50% of observed effect: n per arm = 234 (80% power), 313 (90% power)
power.prop.test: 44.2 
Simulated power at n = 45 per arm: 0.867 (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.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and secondary outcomes, but the statistical plan for handling multiple outcomes is not reported in the registry record. No multiplicity adjustment is reported. When a study evaluates more than one endpoint, repeated testing can increase the chance of a seemingly notable result arising by chance. As a general statistical principle, this makes the distinction between primary and secondary outcomes important: the primary outcome is usually the central prespecified question, while secondary outcomes are interpreted with greater caution unless an analysis plan specifies otherwise.

The registry reports no analyses in its analysis listing. It does not state whether an intention-to-treat, per-protocol, or other analysis population was used. The record also does not describe how participants were handled if they did not receive the assigned timing, whether outcome assessors were blinded, or whether any adjustment for baseline characteristics was conducted. These details are not reported in the registry record and should not be presumed.

Missing-data methods and the amount or pattern of missing outcome information are also not reported. The registry enrollment figure is 64, while the posted outcome denominators are 30 in each group. The record does not explain this relationship. Without participant flow information or an account of missing outcomes, readers cannot determine whether all randomized participants contributed to the posted comparisons or how any unavailable outcomes were treated.

The record does not report interim analyses, stopping rules, a prespecified hypothesis-testing strategy, or whether the posted comparisons were planned before data collection. It also does not provide details of randomization or allocation concealment. These omissions limit evaluation of the risk of selective reporting and the robustness of the comparisons. They do not invalidate the reported counts, but they restrict the conclusions that can be drawn about how the analyses were selected and conducted.

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 0% reporting threshold.

The safety figures report no serious adverse events affecting participants in either group. The serious-adverse-event risk denominators are 30 in the early group and 30 in the late group, and the number affected is zero in each. The posted figures also report zero other adverse events affecting participants in either group, with 30 at risk in each group. Deaths are reported as zero in both groups.

As a general statistical point, observing no events in a group does not establish that the underlying risk is zero. It means no events of that type were recorded in the observed group during the relevant reporting period. With no events, the data provide limited information for estimating the frequency of uncommon harms. The registry record does not describe the adverse-event collection period, definitions, severity grading, or methods for determining whether an event was related to the intervention.

These figures should be read as reported event counts, not as proof that either timing strategy is free of safety concerns. The registry record does not provide a detailed narrative of adverse events or additional safety analyses.

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

The primary results show fewer recorded failed office voiding trials in the late group than in the early group within the stated outcome window. The estimated risk difference is negative for late versus early timing, and its reported confidence interval excludes zero. The unadjusted p-value is 0.023. These statistics describe the observed comparison and its uncertainty; they do not establish a causal mechanism or guarantee that the same difference would appear in another group of patients.

Random allocation is intended to support a fair comparison between groups, but the registry record does not report the allocation procedures or the analysis population. It also does not explain the relationship between the enrollment figure and the posted outcome denominators. Missing-data handling, adherence to assigned timing, and adjustment methods are not reported. The absence of these details limits how confidently the numerical contrast can be attributed to timing alone.

The result applies to the study’s stated context: outpatient pelvic floor surgery among patients whose initial same-day voiding trial failed and who were discharged with a Foley catheter. It does not establish what would happen for patients who passed an initial trial, for other procedures, or outside the study context. The primary endpoint is limited to failures within 8 days of surgery; it is not a measure of longer-term urinary function.

The secondary urinary tract infection result is less conclusive, and the registry record does not report a result for catheter-related bother. The safety record reports no adverse events in the posted categories, but absence of recorded events is not proof of no risk. In general, interpretation should combine the estimated contrast, its precision, the outcome definition, and the limitations of the registry record rather than relying on a single p-value.

17. Why This Trial Matters Statistically

This trial illustrates why the choice of effect measure matters. The risk difference expresses an absolute group contrast, which is directly tied to the difference in event probabilities. Relative measures such as risk ratios and odds ratios answer a related but distinct question. Reporting more than one scale can help readers understand a result, but the measures should not be treated as interchangeable or as separate pieces of evidence when they arise from the same participants and events.

It also illustrates the distinction between statistical evidence and precision. The primary unadjusted p-value is below the planning significance level of 0.05, and the reported risk-difference interval does not include zero. Yet the interval still allows a range of effect sizes. A statistically notable result does not remove uncertainty about the magnitude, and the observed contrast may be sensitive to the small number of posted failures.

The secondary results reinforce the need to distinguish confirmatory questions from exploratory ones. A directionally similar secondary pattern is not equivalent to independent confirmation, especially when outcomes have different definitions and follow-up windows and no multiplicity plan is reported. The unreported catheter-bother result also shows why completeness of outcome reporting matters.

Finally, the record demonstrates the importance of documenting analysis populations, missing-data handling, and original planning assumptions. Without those details, readers can interpret the posted counts and estimates but cannot fully assess the analysis pathway or the relation between enrollment and analyzed participants. Statistical interpretation depends not only on a result’s numerical appearance, but also on how the result was defined and produced.

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 study addresses a specific clinical situation: outpatient pelvic floor surgery followed by failure of an initial same-day voiding trial. The findings should not automatically be extended to other surgical settings or to patients who passed the initial trial. The registry record does not report detailed eligibility criteria or participant characteristics, limiting assessment of how closely the posted groups reflect other patient populations.

The trial is described as randomized but unmasked. The record does not report allocation concealment, who assessed trial failure, or whether the outcome definition was standardized across office visits. These omissions leave uncertainty about implementation and outcome assessment. The assigned timing windows also allow more than one possible day in the early group and an open-ended later timing in the late group; the registry does not explain how the actual appointment day was selected.

The posted primary comparison has 30 participants per group and a limited number of failures. This constrains precision and can make the estimate sensitive to individual outcomes. The registry enrollment figure is 64, but the outcome denominators are 30 per group, and the reason for that difference is not reported. Participant flow, missing outcomes, adherence, and the analysis population are not described.

The analysis record is sparse: no analyses are listed, and the statistical test, multiplicity strategy, interim analyses, and original sample-size justification are not reported. The registry lists catheter-related bother as a secondary outcome without reporting its result. The safety figures also lack a stated collection period and detailed event definitions. These limitations do not change the posted counts, but they restrict evaluation of completeness, reproducibility, and generalizability.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Timing of Repeat Voiding Trials After Outpatient Pelvic Floor Surgery — NCT03048682.
• Registry record last updated 2024-08-21; status last verified 2024-07.
• Results first posted 2024-08-21.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed, randomized, unmasked, parallel-group study sponsored by The Cleveland Clinic. Its title is Timing of Repeat Voiding Trials After Outpatient Pelvic Floor Surgery. The listed enrollment is 64, and the primary endpoint is failed office voiding trials within 8 days of surgery among patients who failed an initial same-day trial and were discharged with a Foley catheter.

The early group was scheduled for a repeat office trial on post-operative day 2, 3, or 4; the late group was scheduled for day 7 or after. The primary outcome counts were 7 in the early group and 1 in the late group, with 30 participants in each posted outcome denominator. The reported risk difference for late versus early timing was -0.2, with a 95% confidence interval from -0.364 to -0.036 and an unadjusted p-value of 0.023.

Urinary tract infections are reported as a secondary outcome within 6 weeks of surgery. Catheter-related bother is listed, but its result is not reported in the registry record. No adverse events or deaths were reported in the posted safety figures. Details of missing-data handling, analysis populations, multiplicity, and the trial’s original sample-size assumptions are not reported.