Value of Urodynamic Evaluation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Value of Urodynamic Evaluation (NCT00803959), a randomized phase 4 study. The primary outcome is Self-reported Urinary Incontinence, Irritative and Obstructive Symptoms: Reduction of 70%+ in the Urogenital Distress Inventory From Baseline to 12 Mos and "Very Much" or "Much" Better on the Patient Global Impression of Improvement Measure at 12 Mos..

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group, Phase 4 trial with no masking. The study is titled “Value of Urodynamic Evaluation,” and its official title is “A Randomized Trial of Urodynamic Testing Before Stress-Incontinence Surgery.” Carelon Research is listed as the sponsor. The trial status is completed.

The population was women who desired surgery for diagnosed, uncomplicated predominant stress urinary incontinence. One arm received a basic office evaluation only; the other received a basic office evaluation plus preoperative urodynamic studies. The registry records 315 women randomized to each arm and enrollment of 630. The primary outcome was assessed at 12 months and combined a specified reduction in Urogenital Distress Inventory (UDI) score with a favorable Patient Global Impression of Improvement (PGI) response.

The registry lists a start of 2008-11 and primary completion of 2009-12. It does not report the random sequence generation method, allocation concealment procedures, or reasons for choosing the enrollment target. It also does not report the original sample-size justification, the trial's planned significance threshold, or a detailed statistical analysis plan. The exact date of final study completion is not reported in the registry record.

Masking was none. Because participants knew whether they received UDS, patient-reported outcomes were collected in an open-label setting. This is relevant to interpretation of reported symptoms and global improvement, though the registry does not describe how outcome collection was conducted or whether any other safeguards were used.

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: 4083 women with urinary incontinence were screened for eligibility; of these 2708 did not meet inclusion criteria, 379 declined to participate and 313 were eligible but excluded for administrative reasons. This left 683 who provided written informed consent; 40 were deemed ineligible before randomization and 13 withdrew consent with 630 randomized.

Overall Study

Analysis population for the primary outcome, as defined in the registry: There were 315 women randomized to each of the arms. In the no UDS arm (and UDS arm), 49 (43) did not have primary outcome data, leaving 266 (272) included in the ITT analysis. Of these, 259 (264) were included in the PP analysis with primary outcome data. The PP analysis was the primary analysis because the outcome was a non-inferiority endpoint.

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 Self-reported Urinary Incontinence, Irritative and Obstructive Symptoms: Reduction of 70%+ in the Urogenital Distress Inventory From Baseline to 12 Mos and "Very Much" or "Much" Better on the Patient Global Impression of Improvement Measure at 12 Mos., measured over 12 Months.

The primary endpoint is a binary measure of treatment success at 12 months. A participant had to meet both parts of the definition: the UDI score had to decrease from baseline by 70% or more, and the participant had to report being “very much better” or “much better” on the Patient Global Impression of Improvement measure. The result is presented as a percentage of participants.

The UDI captures urinary distress, including the urinary incontinence, irritative and obstructive symptoms named in the endpoint description. The PGI adds a patient’s overall impression of improvement rather than relying only on change in a symptom score. Requiring both criteria makes the endpoint a composite: improvement on one measure alone does not meet the stated success definition. The cutoff also distinguishes participants meeting the trial's specified threshold from those who do not.

In general, a binary endpoint can make the proportion meeting a clinically defined criterion straightforward to interpret, but it does not show the full range of symptom changes among participants. People just below the threshold and people with little improvement are grouped together as not meeting the endpoint. The registry lists the primary analysis as per-protocol and also describes an intention-to-treat analysis population. The reasons participants were absent from the primary outcome analysis, and the missing-data handling method, are not reported in the registry record.

7. Results Posted in the Registry

• Urodynamic Testing (UDS Arm): 76.9% (203/264) versus 77.2% (200/259) on control; risk difference -0.3 percentage points (95% CI -7.5 to 6.9), risk ratio 1.00 (0.91–1.09); unadjusted two-proportion z-test p = 0.929.

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.

Percentage Meeting or Exceeding 70% Decrease in UDI Score Between Baseline and 12 Months

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Urodynamic Testing (UDS Arm): 77.2% (210/272) versus 78.9% (210/266) on control; risk difference -1.7 percentage points (95% CI -8.7 to 5.2), risk ratio 0.98 (0.89–1.07); unadjusted two-proportion z-test p = 0.626.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Urodynamic Testing (UDS Arm) and the control. The interval gives the range of effects that remain compatible with the data.

Patient Global Impression Index

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Urodynamic Testing (UDS Arm): 91.9% (248/270) versus 90.8% (238/262) on control; risk difference 1.0 percentage points (95% CI -3.8 to 5.8), risk ratio 1.01 (0.96–1.07); unadjusted two-proportion z-test p = 0.678.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Urodynamic Testing (UDS Arm) and the control. The interval gives the range of effects that remain compatible with the data.

Change in Bother as Measured by the UDI

• 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:
  • Urodynamic Testing (UDS Arm): mean -100.20 versus -98.40 on control; difference -1.80 (95% CI -10.38 to 6.78), standardized effect d = -0.04; z-test p = 0.681.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Urodynamic Testing (UDS Arm) and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies 12 posted secondary outcomes, covering patient-reported improvement, changes in urinary distress and severity, incontinence symptom scores, and quality-of-life measures. Taken together, these outcomes provide additional views of symptoms and patient experience rather than a single independent confirmation of the primary composite. The available secondary comparisons do not establish a consistent separation between the evaluation strategies across these different measures.

Secondary outcomes can help describe whether the primary pattern is accompanied by changes in related domains. They are not interchangeable with the primary endpoint: a change in a symptom scale, a global improvement response, or a quality-of-life score answers a different question from meeting both primary success criteria. The additional measures may therefore add context, but they do not change the definition or analysis population of the primary outcome.

The registry reports unadjusted secondary p-values for the listed analyses and does not report a multiplicity correction or a prespecified hierarchy for interpreting them. In general, examining many outcomes increases the chance that at least one result will appear statistically noteworthy by chance. Unadjusted results should consequently carry less weight than a clearly prespecified primary comparison, and isolated findings should not be treated as confirmatory without the trial's analysis plan and an appropriate multiplicity strategy.

The record lists secondary outcomes beyond the individual secondary results detailed in the available summary. It does not report enough information to assess whether all secondary analyses were prespecified, how missing data were handled for each measure, or whether any analyses were exploratory. The broad pattern is best regarded as supporting descriptive context for the primary result, not as a basis for a definitive conclusion about each outcome domain.

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

• Percentage Meeting or Exceeding 70% Decrease in UDI Score Between Baseline and 12 Months
• Patient Global Impression Index
• Change in Bother as Measured by the UDI
• Change in Severity as Measured by the ISI
• Change in MESA Stress Score
• Change in MESA Urge Score
• Change in Quality of Life as Measured by the IIQ
• Change in Quality of Life as Measured by the SF-12

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help interpret the reported comparison. The primary outcome is binary: each participant either met the combined success definition or did not. The arm-level percentages describe the share meeting that criterion. A difference in percentages compares those shares directly, with the registry specifying the direction as UDS minus office evaluation only. A negative difference therefore points toward a lower success percentage in the UDS arm in this particular coding; it does not by itself indicate whether the difference is important.

What does a chi-squared test assess?

In general, a chi-squared test for a binary outcome assesses whether the observed distribution of success and non-success differs between groups more than would be expected under a null hypothesis of no association. Its p-value measures compatibility between the observed data and that null model, assuming the test's conditions hold. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The registry reports chi-squared as the method for the sponsor's primary comparison.

The recalculated p-value uses posted summary counts and is an unadjusted comparison. It is not a substitute for details of the sponsor's analysis, which are not fully given in the record. Because the discrepancy flag is false, the posted recalculation does not identify a disagreement requiring the sponsor's analysis to be set aside; the sponsor's own reported effect and confidence interval remain the primary reported result.

Why is the confidence interval useful?

In general, a confidence interval describes a range of effect estimates reasonably compatible with the observed data under the method used. A narrow interval indicates greater statistical precision, while a wide interval leaves more uncertainty about the effect size. For the primary outcome, the reported 95% interval for the difference extends from -7.5 to 6.9. Since it includes zero, the result does not rule out no difference; because it also extends on either side of zero, it is compatible with differences favoring either group. A confidence interval is not a guarantee that the true effect lies within its limits.

What do per-protocol and intention-to-treat mean?

In general, an intention-to-treat analysis compares participants according to randomized assignment, regardless of whether they followed the planned intervention, and is intended to retain the benefit of randomization. A per-protocol analysis focuses on participants meeting specified protocol requirements. The registry reports both populations for the primary outcome and identifies per-protocol as the primary analysis. The precise inclusion rules, deviations, and handling of missing outcomes are not reported in the registry record, so the label alone does not explain how participants entered each analysis.

For the primary endpoint, 315 women were randomized to each arm. In the office-evaluation-only arm and UDS arm, respectively, 49 and 43 did not have primary outcome data, leaving 266 and 272 in the intention-to-treat analysis. The per-protocol analysis with primary outcome data included 259 and 264. These figures indicate that outcome availability and analysis-population definitions matter when interpreting the comparison. They do not establish why outcomes were missing or whether the missingness was related to participants' symptoms or outcomes.

What does the non-inferiority label mean?

In general, a non-inferiority analysis asks whether an intervention is not worse than a comparator by more than a prespecified margin. An equivalence analysis asks whether the difference lies within prespecified bounds in both directions. Those margins are essential to the interpretation: a confidence interval must satisfy the relevant criterion, not merely include zero. The registry classifies the primary analysis as non-inferiority-or-equivalence but does not report the margin or decision rule. It is therefore not possible to determine from the record whether a formal non-inferiority or equivalence criterion was met.

For secondary outcomes, the registry reports chi-squared methods for binary comparisons and a two-sided t-test for the change in UDI bother. In general, a two-sided t-test assesses evidence of a difference in means in either direction. The reported secondary p-values are unadjusted, and the record does not report a multiplicity adjustment. As a result, individual secondary p-values should be interpreted cautiously, especially when many outcomes are examined.

11. Confidence Intervals and Precision

The primary sponsor-reported estimate is a difference in success percentages of -0.3 for UDS minus office evaluation only. Its 95% confidence interval is -7.5 to 6.9. The interval spans zero and extends in both directions, so the data do not pinpoint whether the underlying difference favors UDS, favors office evaluation only, or is close to zero. The estimates are compatible with a range of effects, not only with the point estimate.

In general, confidence-interval width reflects statistical precision: wider intervals leave more uncertainty about the size and direction of an effect. The interval does not establish that every value between its endpoints is equally plausible, nor does it give the probability that the true effect lies inside the interval. Its interpretation also depends on the analysis method and the population represented by the data.

For this trial, the registry identifies the per-protocol analysis as primary and records missing primary outcome data in both randomized arms. That context matters because precision is not the same as protection against bias: a confidence interval quantifies sampling uncertainty under the analysis, but it does not resolve possible concerns about missing outcomes or analysis-population selection.

The registry's non-inferiority-or-equivalence classification cannot be evaluated from interval width alone. The margin and decision criteria are not reported in the registry record. Without them, the confidence interval can describe uncertainty around the difference, but it cannot establish formal non-inferiority or equivalence.

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 sample-size illustrations are planning calculations, not a description of the trial's original design target. The entries for this binary primary outcome are participants per arm, rather than total events. The associated curve represents how the planning requirement changes as the effect to detect is varied. For other kinds of outcomes, the stated convention distinguishes participants per arm from total events; these primary-outcome figures are per arm.

The planning 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 to the stated fraction of the observed effect. The trial's own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column indicates the number of participants per arm in a hypothetical study designed to have an 80% chance of detecting the specified effect under those planning assumptions, if that effect is real. The 90% power column uses a higher target chance of detecting it. These are design probabilities under assumed conditions, not probabilities that the trial result is correct or that a treatment is effective. The listed figures are planning illustrations, not observed power.

Smaller effects are harder to distinguish from random variation, so detecting them with the same target power generally requires more participants. The table therefore helps show the relationship between the assumed effect size and a possible future study's enrollment needs. It does not show that the current trial had the listed enrollment for those hypothetical targets, and it does not repair uncertainty arising from missing outcome data or an unreported non-inferiority margin.

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 = 0.772; treatment proportion p₁ = 0.769; average p̄ = 0.771.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5946 = 1.1655.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5946 = 0.5004.
4. n = (1.1655 + 0.5004)² / (-0.0033)² = 260,912.9, rounded up to 260,913 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 <- 0.772200772200772                          # control proportion
p1 <- 0.768939393939394                          # 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(803959)
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 = 260,913 (80% power), 349,288 (90% power)
 75% of observed effect: n per arm = 463,267 (80% power), 620,183 (90% power)
 50% of observed effect: n per arm = 1,041,047 (80% power), 1,393,666 (90% power)
power.prop.test: 260912.9 
Simulated power at n = 260,913 per arm: 0.803 (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. Analyses Reported by the Sponsor

The registry's sponsor-reported primary analysis uses a chi-squared method and describes the comparison as a difference in success percentages, UDS minus office evaluation only. It reports -0.3 with a 95% confidence interval from -7.5 to 6.9. No sponsor p-value is recorded for this primary comparison. The analysis is classified as non-inferiority-or-equivalence, but the margin and formal decision criteria are not reported in the registry record.

The unadjusted recalculation from posted summary counts gives p = 0.929. This is a separate calculation based on those counts and should not be mistaken for a p-value reported by the sponsor. The discrepancy flag is false, so the available recalculation does not indicate a conflict with the sponsor's reported result. The sponsor's analysis remains the relevant trial-reported analysis; the recalculation is supplementary context, not a replacement for the original analysis methods or an extension of what the record establishes.

Neither the sponsor's interval nor the recalculated p-value demonstrates exact equality. Interpreting the result as formal evidence of non-inferiority or equivalence would require the unreported margin and criteria. The most direct reading is that the recorded success percentages were close and that the sponsor-reported interval allows differences in either direction.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome data were unavailable for 49 women in the office-evaluation-only arm and 43 in the UDS arm. The registry reports that 266 and 272 participants, respectively, remained in the intention-to-treat analysis. The per-protocol analysis with primary outcome data included 259 and 264. The record does not explain why outcome data were unavailable, describe the pattern of missingness, or state whether values were imputed. It also does not report the criteria that distinguished the per-protocol population from the intention-to-treat population.

Missing outcomes matter because a comparison based only on observed results can be affected if participants with missing data differ systematically from those with recorded outcomes. This is a general concern, not evidence that such a bias occurred in this trial. Without reasons for missingness and the analysis procedures, the direction or size of any possible effect on the estimates cannot be determined from the registry record.

The per-protocol analysis is identified as primary, while an intention-to-treat analysis is also described. In general, these analysis populations address different aspects of a randomized trial: per-protocol results depend on adherence and protocol-defined inclusion, whereas intention-to-treat results aim to preserve comparison by randomized assignment. The record gives the population counts but not enough methodological detail to evaluate the implications of the difference between them.

The registry records 12 secondary outcomes and 13 analyses. It does not report a multiplicity adjustment, a testing hierarchy, or a strategy for controlling the overall chance of false-positive findings across outcomes. In general, multiple testing can make isolated nominal results less persuasive because the opportunity for chance findings increases with the number of tests. Accordingly, secondary results should be read as supportive or exploratory unless a prespecified analysis plan establishes how they were intended to be interpreted. The original statistical plan and interim-analysis procedures are not reported in the registry record.

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: bladder perforation (5.7%), voiding dysfunction (1.6%), mesh complication: exposure (1.0%), recurrent uti (1.0%), intraoperative bleeding (0.3%).

The registry reports serious adverse events for 30 participants at risk of 315 in the office-evaluation-only arm and 21 at risk of 315 in the UDS arm. It reports other adverse events for 39 participants at risk of 315 in the office-evaluation-only arm and 49 at risk of 315 in the UDS arm. These counts describe the posted safety record; they are not a calculated comparison of risk and should not be read as establishing a safety difference between arms.

The listed serious adverse-event terms and percentages are Bladder Perforation, 5.7%; Voiding dysfunction, 1.6%; Mesh complication: exposure, 1.0%; Recurrent UTI, 1.0%; Intraoperative Bleeding, 0.3%; and Mesh complication: erosion, 0.3%. The registry does not provide event counts for these terms in the information, so the percentages should be read as registry-reported figures rather than converted into counts.

Deaths are not reported in the registry record. The record does not provide enough detail to assess event timing, duration, severity beyond the serious-event classification, or whether events were considered related to a study procedure. These safety figures should therefore be interpreted as descriptive reporting, not as a complete causal comparison of the strategies.

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

The trial compares two preoperative evaluation strategies among women planning surgery for diagnosed, uncomplicated predominant stress urinary incontinence: office evaluation alone and office evaluation with UDS. The primary outcome combines a large specified reduction in UDI score with a favorable PGI response at 12 months. In the per-protocol analysis, the reported success percentages were close, and the sponsor's confidence interval for their difference includes zero.

That result does not prove that the strategies are identical. The interval permits differences in either direction, and the registry does not report the non-inferiority margin needed to judge a formal non-inferiority claim. Nor does a non-significant unadjusted recalculation establish that there is no effect. The data describe uncertainty around a comparison in the analysis population; they do not answer every question about testing, surgical decision-making, or longer-term outcomes.

The result also does not show whether physicians changed their decisions because of UDS, or whether any testing-related change in decisions affected outcomes. Those questions appear in the study background, but the posted primary endpoint is patient-reported success at 12 months. Decision changes are not reported as the primary result. Costs, time burden, discomfort, and total expenditure are also not reported as trial outcomes in the results.

The population is specific. The registry describes women with uncomplicated predominant stress urinary incontinence who desired surgery. The findings should not be generalized from this record to other forms of urinary incontinence, other patient groups, or other clinical contexts without additional evidence. The open-label design and missing primary outcome data are further considerations when interpreting self-reported outcomes.

In short, the posted data show similar observed success percentages in the analyzed groups, with uncertainty that includes differences favoring either strategy. They do not, on their own, establish equivalence, non-inferiority, absence of an effect, or a broader conclusion about the value of urodynamic testing in populations not described by the trial.

18. Why This Trial Matters Statistically

This trial is statistically useful because it frames a diagnostic-testing strategy as a randomized comparison with a patient-reported outcome, rather than treating the number of tests performed as a sufficient measure of value. Its endpoint required both a substantial change in urinary distress and a favorable global assessment. That combined definition illustrates how endpoint construction can affect the question a trial answers: success meant meeting both thresholds, not merely improving on either measure.

The record also highlights the distinction between a non-significant difference and evidence of equivalence. A confidence interval that includes zero does not establish that two strategies are sufficiently alike. For a formal non-inferiority or equivalence conclusion, the margin and decision rule must be specified and the interval assessed against them. The registry identifies the primary analysis with this framework but does not report the information needed to evaluate the formal criterion.

Analysis-population choice is another important statistical issue. The registry identifies a per-protocol analysis as primary and also describes an intention-to-treat population, with missing primary outcomes and different included populations. Those details make transparent reporting of analysis rules and missing-data handling essential for readers assessing how the randomized comparison was preserved.

Finally, the record lists multiple secondary outcomes. Their breadth can help describe patient experience, but it also raises the importance of prespecification and multiplicity control. Without a reported hierarchy or adjustment, secondary findings are less secure as confirmatory evidence. These issues are not unique to this trial; they are general considerations when interpreting randomized evaluations of diagnostic strategies and composite patient-reported endpoints.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations are specific to what the registry reports. The trial was unmasked, and the primary endpoint relies on patient-reported symptom change and global improvement. The registry does not describe the procedures used to collect these reports, so the potential influence of participants' awareness of their evaluation strategy cannot be assessed from the record.

Primary outcome data were unavailable for some randomized participants, and the primary analysis was per-protocol. The registry reports the relevant population counts but not reasons for missing outcomes, the per-protocol inclusion rules, or the missing-data method. These omissions limit assessment of how representative the analyzed participants were of those randomized and how sensitive the result might be to analysis choices.

The primary analysis is labeled non-inferiority-or-equivalence, but the non-inferiority margin and formal decision criteria are not reported. This prevents a reader from determining whether the reported interval satisfies a prespecified non-inferiority or equivalence standard. The record also does not report the original sample-size justification, interim-analysis procedures, or a detailed statistical analysis plan.

The endpoint is assessed at 12 months and uses thresholds on two patient-reported measures. The registry does not establish how results would differ under other endpoint definitions or at other follow-up times. The trial population is restricted to women desiring surgery for uncomplicated predominant stress urinary incontinence, limiting the scope of conclusions based on this record. The reported secondary analyses are unadjusted, and the record does not describe a multiplicity strategy.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Value of Urodynamic Evaluation — NCT00803959.
• Registry record last updated 2013-08-06; status last verified 2013-07.
• Results first posted 2013-08-06.
• 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, parallel-group, unmasked Phase 4 trial sponsored by Carelon Research. It enrolled 630 women planning surgery for uncomplicated predominant stress urinary incontinence, with 315 randomized to office evaluation only and 315 to office evaluation plus preoperative UDS.

The primary outcome was success at 12 months, defined by both a 70% or greater reduction in UDI score and a PGI response of “very much better” or “much better.” The per-protocol success percentages were 77.2% for office evaluation only and 76.9% for UDS. The sponsor reported a difference of -0.3 and a 95% confidence interval from -7.5 to 6.9.

The registry classifies the primary analysis as non-inferiority-or-equivalence, but does not report the margin needed to assess that claim. It also records missing primary outcome data, reports both per-protocol and intention-to-treat populations, and does not describe the missing-data method. The posted result is compatible with differences in either direction and does not establish equivalence.