Outcomes of Anterior Colporrhaphy Versus Graft Reinforced Anterior Prolapse Repair: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Outcomes of Anterior Colporrhaphy Versus Graft Reinforced Anterior Prolapse Repair (NCT00535301), a randomized phase 4 study. The primary outcome is Recurrent Stage II or Greater Anterior Vaginal Prolapse.

2. Clinical Question

3. Trial Design

This is a completed, randomized, double-blind, parallel-group, phase 4 trial sponsored by Kaiser Permanente. The registry record lists enrollment of 75. The study started in 2005-01 and primary completion was 2008-04. The two arms were anterior colporrhaphy, a sutured repair without graft, and Perigee, a grafted anterior prolapse repair.

The primary outcome is a binary participant count: whether recurrent stage II or greater anterior vaginal prolapse was recorded at three years. The posted primary outcome population is intention to treat. The registry record defines the recurrence threshold using the POPQ Ba measurement. The outcome records list 38 participants in each arm, with 24 events in the anterior colporrhaphy arm and 11 in the Perigee arm.

Random allocation helps make the treatment groups comparable in expectation, but does not guarantee that every characteristic is balanced in a particular trial. The record identifies the study as double-blind but does not report who was masked or how masking was implemented. It also does not report the randomization procedure or concealment details, so those aspects cannot be evaluated from this record.

The listed secondary outcomes are operative time and vaginal mesh exposure. The posted results include a vaginal mesh exposure outcome; operative time is listed among secondary outcomes, but its numeric result is not reported in the registry record. The record describes the trial as completed. The original sample-size justification, operational details of follow-up, and trial-specific statistical plan 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: Exclusion criteria were less than stage II anterior vaginal prolapse, current or future pregnancy, prior grafted anterior prolapse repair, impaired wound healing, known hypersensitivity to polypropylene, unable or unwilling to give valid informed consent or if scheduled to undergo concomitant Burch colposuspension or pubovaginal sling.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intention to Treat. Stage II or greater anterior vaginal prolapse was defined as POPQ Ba equal to or greater than -1.

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 Recurrent Stage II or Greater Anterior Vaginal Prolapse, measured over three years.

The primary endpoint is the number of participants with recurrent stage II or greater anterior vaginal prolapse at three years. It is a binary outcome: each participant is classified according to whether the recurrence definition is met. The registry record defines recurrence as a POPQ Point Ba measurement equal to or greater than -1.

Point Ba describes the most distal position of the anterior vaginal wall between point Aa and the vaginal cuff or anterior vaginal fornix. The record explains that more negative values indicate better support, with -3 cm assigned when there is no prolapse, while positive values indicate prolapse beyond the hymen and worse support. Applying a defined threshold turns this anatomical measurement into a count of participants with or without recurrence.

In general, a prespecified clinical endpoint provides a consistent basis for comparing randomized groups. A binary endpoint can be interpreted in terms of the proportion experiencing the event and the difference between those proportions. It also makes the outcome threshold explicit, though it does not describe every possible degree of anatomical change. The reported endpoint therefore addresses recurrence under the registry definition; it should not be interpreted as a comprehensive measure of every symptom, complication, or aspect of recovery.

7. Results Posted in the Registry

• Perigee: 28.9% (11/38) versus 63.2% (24/38) on control; risk difference -34.2 percentage points (95% CI -55.3 to -13.2), risk ratio 0.46 (0.26–0.80); unadjusted two-proportion z-test p = 0.003.

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.

Vaginal Mesh Exposure

• 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:
  • Perigee: 10.5% (4/38) versus 0.0% (0/38) on control; risk difference 10.5 percentage points (95% CI 0.8 to 20.3); unadjusted two-proportion z-test p = 0.040.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Perigee than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes concern aspects of the procedures that are distinct from recurrence: operative time and vaginal mesh exposure. The record lists both outcomes, but numeric posted results are not present for every listed secondary outcome. The pattern across secondary outcomes therefore cannot be fully characterized from the registry record. In particular, the numeric result for operative time is not reported in the registry record.

Secondary outcomes can help describe dimensions of the intervention that the primary endpoint does not capture. They should not be treated as interchangeable with the primary endpoint: an anatomical recurrence measure, a procedure-time measure, and a device-exposure measure represent different questions. The secondary findings do not alter the definition or interpretation of the three-year recurrence outcome.

The registry record does not report whether a multiplicity adjustment was planned or applied. When several outcomes are tested, the chance of at least one apparently notable result can rise if each is interpreted as though it were the only test. For that reason, unadjusted secondary results generally carry less confirmatory weight than a prespecified primary analysis, especially when the analysis plan and outcome hierarchy are not documented. This is a general statistical caution, not evidence that any particular secondary finding is false.

The available secondary information can be considered alongside the primary result as descriptive context, but it does not establish an overall benefit-harm balance. The missing outcome details and the absence of reported multiplicity procedures limit how strongly secondary comparisons can support broader conclusions.

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

• Operative Time
• Vaginal Mesh Exposure

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

For a binary endpoint, the risk in a group is the proportion of participants counted as having the event. A risk difference subtracts one group’s risk from the other’s. In this comparison, the stated direction is Perigee minus anterior colporrhaphy, so a negative estimate indicates fewer observed events in the Perigee group. The estimate is -0.342. A risk difference is an absolute contrast on the probability scale, not a relative measure. It can be read as a difference between the event proportions, while its confidence interval expresses uncertainty about that contrast.

How does an odds ratio differ?

An odds ratio compares the odds of an event between groups. Odds and risks are related but are not the same quantity, so an odds ratio cannot be substituted for a risk difference. The registry record reports an odds ratio of 0.24 for the primary comparison. An odds ratio of 1 is the no-association reference value; estimates below 1 indicate lower event odds in the numerator group relative to its comparator, given the stated group order. Interpretation depends on that order and on the outcome definition.

What do the p-values say?

A p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The recalculated unadjusted risk-difference analysis gives p = 0.003. The registry’s chi-squared analysis reports p = 0.005 for the odds ratio. These are results from different analyses and effect scales. Neither p-value gives the probability that the finding will replicate.

Why are different tests reported?

The posted recalculation uses summary event counts to form an unadjusted comparison of proportions and a risk difference. The registry analysis is identified as chi-squared and reports an odds ratio. For categorical data, a chi-squared test evaluates whether observed group counts are compatible with a no-association hypothesis under its assumptions. Fisher’s exact test is also reported for vaginal mesh exposure. In general, Fisher’s exact test calculates inference from the possible allocations of counts under its null model and can be useful when counts are sparse. The registry record does not report the full details of how each analysis was implemented.

These methods answer related but not identical statistical questions. Differences in effect scale, test construction, and rounding can lead to different estimates or p-values without implying a contradiction. The record does not mark a discrepancy for the primary comparison. The sponsor’s reported analysis should be distinguished from the unadjusted re-calculation rather than treated as if it were the same calculation.

What does intention to treat mean?

The primary outcome population is identified as intention to treat. In general, an intention-to-treat analysis evaluates participants according to their randomized group, regardless of subsequent treatment received, when the analysis is implemented according to that principle. This preserves the randomized comparison and estimates the effect of assignment to the study groups. The registry record does not describe how missing outcomes, withdrawals, or deviations from assigned treatment were handled, so implementation details cannot be assessed.

Why can over-dispersion matter?

Over-dispersion is a general issue for count outcomes when observed variability exceeds what a model’s assumed distribution allows. In such settings, standard errors can be too small if the extra variability is ignored. It is not a stated feature of this primary endpoint: the outcome is a binary participant count, not a rate or continuous count process, and the dispersion field is not populated. Therefore, there is no basis in the registry record to claim that over-dispersion was present or that a particular adjustment was used.

What is not documented?

The trial-specific statistical analysis plan, the original sample-size justification, any interim analyses, and details of missing-data handling are not reported in the registry record. The reported primary analysis and the posted event counts support interpretation of the registered comparison, but they do not reveal every planned or performed analytic decision. General descriptions of statistical methods should not be mistaken for confirmation that a particular procedure was part of the trial protocol.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.342, with a 95% confidence interval from -0.553 to -0.132. A confidence interval gives a range of effect values reasonably compatible with the data and the calculation’s assumptions. It conveys precision as well as direction: a wider interval indicates more uncertainty about the magnitude, while an interval concentrated near a value indicates greater precision around that value.

For the risk difference, zero represents no difference between groups. The reported interval lies below zero, so the range of values compatible with this calculation points toward a lower observed event proportion in the Perigee arm. The interval nevertheless includes a range of possible magnitudes. It should not be reduced to a single claim based only on the point estimate.

The registry’s odds-ratio analysis reports 0.24 with a 95% confidence interval from 0.1 to 0.6. For an odds ratio, 1 is the null value. This interval is on the odds-ratio scale and cannot be compared numerically with the risk-difference interval. Each interval must be interpreted using its own measure and reference value.

Confidence intervals do not account for every source of uncertainty. They do not automatically address bias from missing data, outcome measurement, deviations from protocol, or unreported analytic choices. The registry record does not report all of those details. Precision in the statistical estimate should therefore be distinguished from certainty about generalizability or the full clinical balance of outcomes.

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 figures are planning illustrations based on the observed primary effect, not the trial’s original design. The assumptions listed for these illustrations 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 as the stated fraction of the observed effect. The trial’s own design assumptions and original sample-size justification are not reported in the registry record.

The figures are participants per arm for 80% power and participants per arm for 90% power. In plain terms, the 80% column gives the planned number in each group under the stated assumptions for a design with 80% power to detect the chosen effect. The 90% column gives the corresponding number per group for a design targeting 90% power. These are planning quantities, not descriptions of the actual number enrolled in the trial.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so it requires more participants to reach the same target power under the same assumptions. The sample-size curve should be read as a visual representation of how the required group size changes across effect assumptions, not as a record of what the trial planned or achieved.

This is not observed power. It is a forward-looking illustration computed from the observed effect and stated assumptions; it does not measure the probability that the trial’s result is true or provide an additional test of the result. Because the observed effect is used as the starting point, the illustration should not be taken as an independent confirmation of the primary finding.

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 = 0.632; treatment proportion p₁ = 0.289; average p̄ = 0.461.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7049 = 1.3816.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6621 = 0.5572.
4. n = (1.3816 + 0.5572)² / (-0.3421)² = 32.1, rounded up to 33 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 <- 0.631578947368421                          # control proportion
p1 <- 0.289473684210526                          # 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(535301)
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 = 33 (80% power), 43 (90% power)
 75% of observed effect: n per arm = 59 (80% power), 78 (90% power)
 50% of observed effect: n per arm = 132 (80% power), 176 (90% power)
power.prop.test: 32.1 
Simulated power at n = 33 per arm: 0.845 (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 reported primary analysis uses a chi-squared method and gives an odds ratio of 0.24, a 95% confidence interval from 0.1 to 0.6, and p = 0.005. The simple unadjusted re-calculation uses the posted counts to express the comparison as a risk difference of -0.342, with a 95% confidence interval from -0.553 to -0.132 and p = 0.003.

These results are related but are not identical statistics: the odds ratio and risk difference use different scales, and their associated inference comes from different analytic formulations. Their p-values therefore need not match. The registry record does not flag a discrepancy for this comparison. The re-calculation is not a replacement for the sponsor’s stated analysis, and the record does not provide enough detail to reconstruct every aspect of that analysis.

Both the reported odds-ratio interval and the recalculated risk-difference interval fall on the side indicating fewer observed events in the grafted arm, relative to the sutured arm, for the primary endpoint. Interpretation should retain the distinction between the sponsor’s reported model-based summary and the unadjusted summary-statistic comparison. The registry’s reported analysis is the trial’s own posted result; the re-calculation offers a complementary expression of the group contrast.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one endpoint, comparison, or analysis. In general, repeated testing can increase the chance of at least one result appearing statistically notable by chance. Prespecified hierarchies, adjusted procedures, or clearly designated exploratory analyses can help readers understand how multiple results were handled. The registry record does not report a multiplicity strategy, so it is not possible to determine whether adjustments were planned or applied.

The record identifies a primary endpoint and lists secondary outcomes, which distinguishes the main question from additional questions. However, it does not provide the full statistical analysis plan, the ordering of all analyses, or whether additional analyses were conducted. The existence of a named primary outcome does not by itself establish how every other statistical test was controlled or interpreted.

The primary population is described as intention to treat. This identifies the intended analysis population, but the registry record does not report how missing primary outcome measurements were treated, whether participants were excluded from particular analyses, or how follow-up completeness was assessed. Those details matter because missing outcomes can affect both the estimated event proportions and the uncertainty around the comparison.

The outcome counts show 38 participants in each arm, while registry enrollment is listed as 75. These are different registry fields; the record does not explain their relationship or provide a participant flow accounting that would clarify it. No inference about the reason for this difference should be made from the posted information alone.

Interim analyses, stopping rules, the trial’s own sample-size justification, and details of randomization implementation are also not reported in the registry record. These omissions do not invalidate the posted results, but they limit assessment of how the study was planned and whether all analysis decisions can be evaluated. The conclusions should therefore remain anchored to the endpoints and statistics that are actually reported.

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 5% reporting threshold.

The serious adverse event figures list zero affected participants among 38 at risk in each arm. The record also lists zero other adverse events among 38 at risk in the anterior colporrhaphy arm and among 37 at risk in the Perigee arm. These are registry counts for the categories shown, not proof that no adverse event of any kind occurred or that the procedures have no risks.

The deaths fields are not populated, so death counts are not reported in the registry record. The record lists no serious adverse event terms. Without further detail about event definitions, collection procedures, follow-up completeness, or severity classification, the counts should be read narrowly as the posted adverse-event summary.

Zero observed events in a group do not establish that the underlying event risk is zero. Safety interpretation depends on the amount and duration of observation as well as the event definitions and reporting process. The registry record does not provide enough information to quantify rare-event risk or to compare overall safety comprehensively. These adverse-event figures should be considered alongside, not as a substitute for, the primary and secondary outcome results.

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

The primary result describes the observed frequency of a specifically defined anatomical recurrence at three years in two randomized treatment groups. In the posted counts, fewer participants in the Perigee arm met the recurrence definition than in the anterior colporrhaphy arm. The recalculated risk difference and its confidence interval quantify the direction and uncertainty of that observed comparison.

The result does not establish that every participant benefits from grafted repair, that the same difference will occur in another setting, or that all outcomes favor one approach. A group-level estimate does not predict an individual participant’s result. Nor does the primary endpoint capture every possible feature of recovery, symptoms, quality of life, procedure burden, or complications.

The study’s stated purpose includes both effectiveness and complications. The primary recurrence endpoint addresses only one part of that question. Secondary outcomes include operative time and vaginal mesh exposure, but complete numeric reporting is not available for all listed outcomes. The posted adverse-event counts also have limits and do not establish the absence of risk.

Statistical evidence and clinical importance are related but distinct. A p-value addresses compatibility with a null model under test assumptions; it does not determine whether the size of the observed difference matters to patients or clinicians. The confidence interval helps convey plausible effect magnitudes but does not resolve questions about outcome relevance, generalizability, missing data, or unreported analytic decisions.

The most defensible interpretation is therefore bounded: the registry’s primary data show a group difference in the observed recurrence endpoint, with the grafted group having fewer recorded events in this trial. Further conclusions about the overall merits of either procedure require evidence beyond this single endpoint and the incomplete secondary and safety information in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of effect measure matters. A risk difference communicates an absolute contrast between event proportions, while an odds ratio expresses a relative contrast in odds. Both can describe the same underlying comparison, but the scales answer different interpretive needs and should not be interchanged. Reporting both the registry analysis and a transparent unadjusted re-calculation helps readers distinguish these summaries.

The endpoint also demonstrates how a continuous anatomical measure can be converted into a binary outcome using a stated threshold. That makes the event definition operational and supports a clear comparison of counts, but it also compresses information: participants just on either side of the threshold are classified differently, while variation within each category is not represented by the event count.

Precision is important alongside statistical significance. The confidence interval communicates uncertainty around the primary contrast, rather than leaving interpretation to a single p-value. The planning illustrations further show, in general, why the number of participants needed depends on the effect size a study aims to detect. They are not evidence about the trial’s original planning or the reliability of its observed result.

Finally, registry records make the boundary between reported and unreported information visible. Here, the primary analysis and some secondary and safety counts are posted, while the trial-specific analysis plan, missing-data methods, multiplicity approach, and some outcome results are not. Recognizing those limits is part of sound statistical interpretation, particularly when a trial’s stated question spans both effectiveness and complications.

19. Limitations

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

The primary comparison has a modest number of participants in the posted outcome groups, which limits the amount of information available for estimating event rates and examining uncommon outcomes. The confidence interval shows that the magnitude of the risk difference remains uncertain. The registry record does not provide subgroup results or enough detail to assess whether the observed comparison varies across participant characteristics.

The primary endpoint is a thresholded anatomical measure. It reports whether the recurrence definition was met, but does not convey the full distribution of POPQ Ba measurements or how close individual measurements were to the threshold. The record does not report patient-reported outcomes alongside the primary endpoint, so the relationship between anatomical recurrence and participants’ symptoms or experience cannot be assessed from these results.

The registry record does not report the original sample-size justification, detailed randomization or masking procedures, missing-data handling, interim analyses, or the full statistical analysis plan. It also does not explain the relationship between the enrollment listing and the primary outcome arm counts. The numeric operative-time result is not reported in the registry record, and death counts are not reported.

These limitations concern what can be evaluated from the posted record; they do not establish that a particular design or analysis feature was absent. The result should be interpreted as a comparison within this trial, with attention to the defined endpoint, available follow-up information, and uncertainty in the estimates. Broader conclusions require consideration of additional outcomes and evidence beyond the posted primary comparison.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Outcomes of Anterior Colporrhaphy Versus Graft Reinforced Anterior Prolapse Repair — NCT00535301.
• Registry record last updated 2015-04-22; status last verified 2015-04.
• Results first posted 2011-07-28.
• 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

NCT00535301 is a completed, randomized, double-blind, parallel-group, phase 4 trial sponsored by Kaiser Permanente. It compares anterior colporrhaphy without graft with Perigee grafted anterior prolapse repair. The registry lists enrollment of 75 and primary completion in 2008-04.

The primary outcome is recurrent stage II or greater anterior vaginal prolapse at three years, defined using POPQ Point Ba. The posted counts are 24 of 38 in the sutured repair arm and 11 of 38 in the grafted repair arm. The registry reports a chi-squared odds ratio of 0.24, with a 95% confidence interval from 0.1 to 0.6 and p = 0.005. An unadjusted risk-difference re-calculation is -0.342, with a 95% confidence interval from -0.553 to -0.132 and p = 0.003.

Secondary outcomes listed include operative time and vaginal mesh exposure. The record does not report numeric operative-time results or a complete trial-specific analysis plan. The posted primary comparison indicates a difference in the defined recurrence outcome, while uncertainty and incomplete reporting limit broader conclusions about all outcomes and overall safety.