A Study to Evaluate the Efficacy and Safety of Vedolizumab in the Treatment of Chronic Pouchitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy and Safety of Vedolizumab in the Treatment of Chronic Pouchitis (NCT02790138), a randomized phase 4 study. The primary outcome is Percentage of Participants With Chronic or Recurrent Pouchitis Achieving Clinically Relevant Remission at Week 14.

2. Clinical Question

3. Trial Design

This was a Phase 4, randomized, double-blind, placebo-controlled, parallel-group study of vedolizumab for chronic pouchitis. The registry record describes quadruple masking. It lists an enrollment of 102 and a completed status. The study start date was 2016-10-12, and the primary completion date was 2020-06-11.

The comparison was between Vedolizumab IV 300 mg and Placebo IV. Both groups also received ciprofloxacin 500 mg orally twice daily up to Week 4. The vedolizumab or matching placebo infusions were scheduled at Day 1 and Weeks 2, 6, 14, 22, and 30. The record does not identify which roles were included in the quadruple masking, or provide further details of the allocation procedure.

The primary outcome was clinically relevant remission at Week 14. Its analysis population was the Full Analysis Set, defined in the record as randomized participants who received at least 1 dose of study medication, analyzed as randomized. Each arm has 51 participants in the posted primary outcome results. This outcome is a percentage: a participant either met the stated remission definition by Week 14 or did not.

The record also lists secondary outcomes covering remission at Week 34, PDAI and partial mPDAI response, time to PDAI remission, changes in disease activity measures, and change in IBDQ total score. These address related clinical and patient-reported domains, but they do not replace the prespecified primary comparison. The registry record does not report the original design assumptions or a detailed account of study conduct beyond the information.

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: Participants with a diagnosis of chronic or recurrent pouchitis were enrolled in a 1:1 ratio to receive placebo IV or vedolizumab IV 300 mg.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) included all randomized participants who received at least 1 dose of study medication, as randomized.

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.

Population: Full Analysis Set included all randomized participants who received at least 1 dose of study medication, as randomized.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Chronic or Recurrent Pouchitis Achieving Clinically Relevant Remission at Week 14, measured over Week 14.

The primary endpoint is the percentage of participants with chronic or recurrent pouchitis who achieved clinically relevant remission at Week 14. Remission required both an mPDAI score below 5 and a reduction of at least 2 points from Baseline. Because both conditions had to be met, the endpoint captures a defined state of disease activity and improvement rather than a change in score alone.

The mPDAI combines clinical symptoms and endoscopic inflammation findings. Its total score ranges from 0, the best score, to 12, the worst; higher scores indicate more severe disease. The clinical subscore includes stool frequency, rectal bleeding, urgency or abdominal cramps, and fever. The endoscopic subscore records findings including edema, granularity, friability, loss of vascular pattern, mucous exudates, and ulcerations.

A remission percentage is useful for a randomized comparison because it expresses how often participants in each group met the same clinical definition by a specified visit. It does not describe every change in symptoms or endoscopic findings, and it does not show how far from the threshold each participant was. The Week 14 outcome is therefore a focused binary measure, interpreted alongside its confidence intervals and the other outcomes rather than as a complete account of disease status.

7. Results Posted in the Registry

• Vedolizumab IV 300 mg: 31.4% (16/51) versus 9.8% (5/51) on control; risk difference 21.6 percentage points (95% CI 6.4 to 36.7), risk ratio 3.20 (1.27–8.08); unadjusted two-proportion z-test p = 0.007.

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 of Participants With Chronic or Recurrent Pouchitis Achieving Clinically Relevant Remission at Week 34

• 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:
  • Vedolizumab IV 300 mg: 35.3% (18/51) versus 17.6% (9/51) on control; risk difference 17.6 percentage points (95% CI 0.9 to 34.4), risk ratio 2.00 (0.99–4.03); unadjusted two-proportion z-test p = 0.043.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Vedolizumab IV 300 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time to PDAI Remission

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor; it was not recalculated.
• Result:
  • Placebo IV vs Vedolizumab IV 300 mg: hazard ratio 3.95 (95% CI 1.70–9.40) (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically higher for Placebo IV vs Vedolizumab IV 300 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several related aspects of pouchitis, including later remission, time to PDAI remission, PDAI remission, partial mPDAI response, disease activity subscores, total PDAI, and IBDQ. The Week 34 clinically relevant remission result is directionally consistent with the Week 14 primary comparison: the observed percentage is higher in the vedolizumab group. The time-to-remission outcome has a reported hazard ratio, but the record does not give the event coding and model details needed to independently establish its direction or interpretation.

The record lists 9 secondary outcomes and 19 analyses, but detailed numerical results are not available for every listed measure in the registry account. It is therefore not possible to characterize the full set of secondary findings as uniformly consistent or inconsistent with the primary result. The outcomes also measure different constructs and use different scales, so they should not be combined into a single overall estimate without a specified method.

General: secondary analyses can help assess whether a primary result is accompanied by changes in related outcomes, but multiple testing increases the chance of finding at least one apparently positive result. No multiplicity adjustment is reported in the registry record. These analyses therefore provide supportive or exploratory context rather than automatic confirmation of the primary comparison. Their interpretation should account for the endpoint definitions, time points, analysis methods, and the fact that the primary question was defined at Week 14.

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

• Percentage of Participants With Chronic or Recurrent Pouchitis Achieving Clinically Relevant Remission at Week 34
• Percentage of Participants Achieving Pouchitis Disease Activity Index (PDAI) Remission at Weeks 14 and 34
• Time to PDAI Remission
• Percentage of Participants Achieving a Partial mPDAI Response at Weeks 14 and 34
• Change From Baseline in PDAI Endoscopic Inflammation Subscore at Weeks 14 and 34
• Change From Baseline in PDAI Acute Histologic Inflammation Subscore at Weeks 14 and 34
• Change From Baseline in Total PDAI Score at Weeks 14 and 34
• Change From Baseline in Inflammatory Bowel Disease Questionnaire (IBDQ) Total Score at Weeks 14, 22, and 34

9. Statistical Interpretation

10. Statistical Methods Explained

General: a binary endpoint divides participants into outcome categories. For this primary outcome, a participant either met the Week 14 remission definition or did not. The arm percentages describe the observed proportion meeting that definition. The comparison can be expressed as an absolute percentage difference, while tests can assess how compatible the observed group contrast is with a null hypothesis of no difference.

What does the reported test assess?

The registry identifies Fisher's Exact Test for the sponsor-reported primary comparison. This test is used for categorical outcomes and evaluates the association between randomized group and outcome using the observed event counts. The sponsor reported a percentage difference of 21.6, a 95% confidence interval from 4.9 to 37.5, and p = 0.013. The result is classified as a superiority analysis. A p-value describes how unusual results at least as incompatible with the null hypothesis would be if that null model and the test assumptions held; it is not the probability that the null hypothesis is true or that the result occurred by chance.

The re-calculation is an unadjusted comparison using the posted counts: 5 remission outcomes among 51 participants in the placebo arm and 16 among 51 in the vedolizumab arm. Its reported unadjusted p-value is 0.007. This is a separate calculation from the sponsor's Fisher's Exact Test result, and it is not an adjusted analysis. A p-value can vary with the test and calculation choices, even when based on the same observed counts. The re-calculation is best read as a check on the posted summary rather than as a replacement for the sponsor's analysis.

What do the confidence intervals describe?

General: a confidence interval gives a range of values compatible with the data and the interval procedure, under its assumptions. The arm-specific intervals describe uncertainty in each remission percentage. The sponsor's interval describes uncertainty in the percentage difference. An interval is not a guarantee that the true value lies within its limits, and its width is informative about precision. The reported interval for the primary difference lies above zero, which aligns with the sponsor's superiority classification.

Why distinguish a risk difference from a ratio?

General: an absolute difference describes how far apart the outcome percentages are on the percentage-point scale. A relative measure instead compares one group's outcome frequency with another group's frequency. These answer different questions and can give different impressions of the same data. The sponsor's reported primary result is a percentage difference, so it is the most direct scale for describing the posted analysis. The registry also contains recalculated ratio measures, but the sponsor-reported analysis should remain central to interpretation.

What does the analysis population mean?

The primary population is the Full Analysis Set: randomized participants who received at least 1 dose of study medication, analyzed as randomized. This definition retains participants in their randomized groups for the reported analysis, while excluding randomized participants who received no dose. It is not identical to an analysis of every randomized participant regardless of treatment receipt. The registry record does not provide a separate account of how missing Week 14 outcomes were handled, whether imputation was used, or whether sensitivity analyses were conducted.

What can be inferred from secondary analyses?

The record lists 9 secondary outcomes and 19 analyses. Secondary measures address remission at another visit, time to remission, disease activity, endoscopic and histologic subscores, and IBDQ. The displayed inferential method differs by outcome: the Week 34 remission analysis is reported with a Chi-squared Test, while time to PDAI remission is reported as a hazard ratio with a confidence interval. General: time-to-event methods account for the timing of an event and may also handle participants whose event time is not observed during follow-up, depending on the analysis. The details of the time-to-event model, censoring, and event coding are not reported in the registry record.

Testing multiple outcomes creates more opportunities for an apparently noteworthy result. Whether the trial used a multiplicity procedure, and which outcomes or analyses it covered, is not reported in the registry record. Consequently, secondary p-values should be interpreted cautiously and do not automatically carry the same confirmatory weight as the primary analysis. No additional statistical plan or interim analysis details are reported in the registry record.

11. Confidence Intervals and Precision

The Week 14 arm estimates have 95% confidence intervals of 3.3% to 21.4% for placebo and 19.1% to 45.9% for vedolizumab. These intervals convey substantial uncertainty about the underlying remission percentages: each is a range of plausible values under the interval method, not an exact description of the population rate. The intervals overlap, but overlap between separate arm intervals is not itself the formal test of the difference between arms.

For the primary comparison, the sponsor reports a percentage difference of 21.6, with a 95% confidence interval from 4.9 to 37.5. This interval is more directly relevant to the group contrast than the two separate arm intervals. Its lower limit is above zero, consistent with the reported p = 0.013 and the superiority classification. The interval nevertheless spans a range of possible differences, so the point estimate should not be treated as known without uncertainty.

General: confidence interval width reflects precision, which depends on factors such as sample information, outcome frequency, and the interval method. Wider intervals indicate less precision; narrower intervals indicate more. A confidence interval does not account for every possible source of uncertainty, such as bias, limitations in outcome ascertainment, or unreported analysis decisions. The registry record does not report enough detail about missing outcomes or sensitivity analyses to assess their influence on precision.

The Week 34 remission analysis also has an interval for its reported difference, and the time-to-remission analysis has a confidence interval for the hazard ratio. Those intervals concern different estimands and should not be read as interchangeable with the primary percentage-difference interval. Precision is therefore outcome-specific, and the Week 14 primary estimate should be interpreted on its own scale and at its stated time point.

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 effect, not the trial's original design assumptions. For binary outcomes, the figures are participants per arm. For time-to-event outcomes, the figures are total events. 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 the stated fraction of the observed effect.

For the primary Week 14 outcome, planning for 100% of the observed effect gives 54 participants per arm for 80% power and 72 participants per arm for 90% power. Planning for 75% of the observed effect gives 87 participants per arm for 80% power and 116 participants per arm for 90% power. Planning for 50% of the observed effect gives 173 participants per arm for 80% power and 231 participants per arm for 90% power.

In plain language, the 80% column describes a planning scenario with an 80% chance of detecting the specified effect if the assumptions hold; the 90% column uses a higher target chance of detection for that same specified effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm in these illustrations. These figures are not observed power and do not show the probability that the trial's finding is true. The registry record does not report the original sample-size justification or the assumptions used to design the completed trial.

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 = 0.098; treatment proportion p₁ = 0.314; average p̄ = 0.206.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5718 = 1.1208.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5511 = 0.4638.
4. n = (1.1208 + 0.4638)² / (0.2157)² = 54.0, rounded up to 54 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 <- 0.0980392156862745                          # control proportion
p1 <- 0.313725490196078                          # 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(2790138)
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 = 54 (80% power), 72 (90% power)
 75% of observed effect: n per arm = 87 (80% power), 116 (90% power)
 50% of observed effect: n per arm = 173 (80% power), 231 (90% power)
power.prop.test: 54 
Simulated power at n = 54 per arm: 0.815 (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 sponsor's primary analysis reports a percentage difference of 21.6, with a 95% confidence interval from 4.9 to 37.5 and p = 0.013, using Fisher's Exact Test. It is the registry's reported superiority analysis and should anchor interpretation of the trial result.

The unadjusted re-calculation is based on the posted remission counts and uses a separate calculation; its p-value is 0.007. It is not an attempt to reproduce every aspect of the sponsor's analysis, and it does not replace the analysis method reported by the sponsor. The registry does not flag a discrepancy between the posted result and the re-calculation. Differences between p-values can arise because analyses use different test procedures or inferential methods.

The estimates are directionally consistent: both describe a higher observed Week 14 remission percentage in the vedolizumab arm. The sponsor's reported percentage difference and its confidence interval are the more appropriate figures for stating the trial's own primary result. The re-calculation serves as a simple unadjusted check on the summary data; it should not be treated as an independent replication or as a second trial result.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome is clearly identified as clinically relevant remission at Week 14, with the Full Analysis Set specified. The registry also lists 9 secondary outcomes and 19 analyses. This creates a multiplicity issue: when many outcomes or comparisons are assessed, the chance of at least one nominally significant finding can increase. Whether any adjustment was planned or applied is not reported in the registry record. The record does not identify a hierarchy of secondary outcomes or state which analyses, if any, were intended to be confirmatory.

The registry defines the primary analysis population as randomized participants who received at least 1 dose of study medication, analyzed as randomized. It does not report the number of participants with missing Week 14 outcome data, the reason for any missing observations, or how missing outcomes were handled. Imputation, complete-case analysis, and sensitivity analyses are not reported in the registry record. Without those details, the effect of missing data on the primary estimate cannot be evaluated from this account.

The record identifies a sponsor-reported Fisher's Exact Test for the primary comparison and a Chi-squared Test for Week 34 remission. It reports a hazard ratio for time to PDAI remission, but the time-to-event model, event coding, and censoring rules are not reported in the registry record. The original statistical analysis plan, interim analyses, and the trial's original sample-size justification are also not reported in the registry record. These omissions limit assessment of whether the reported analyses followed a prespecified strategy and how secondary inferences should be calibrated.

General: a prespecified plan helps distinguish the main hypothesis from additional analyses and makes selective emphasis less likely. Missing-data sensitivity analyses assess whether conclusions depend on assumptions about unobserved outcomes. Neither principle can be assessed fully without the relevant details; their absence from the registry record should not be filled by assumptions.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pouchitis (3.9%), abdominal pain (2.0%), intestinal obstruction (2.0%), gastroenteritis (2.0%), basal cell carcinoma (2.0%).

The serious adverse event figures are reported by randomized group. In the placebo group, 4 participants were reported with a serious adverse event among 51 at risk; in the vedolizumab group, 3 were reported among 51 at risk. The record reports 0 deaths in each group. These are counts within the stated groups, not estimates adjusted for exposure time or differences in follow-up.

For other adverse events, the record reports 35 participants affected among 51 at risk in the placebo group and 42 among 51 at risk in the vedolizumab group. The registry also lists serious-event terms and their percentages: Pouchitis, 3.9%; Abdominal pain, 2.0%; Intestinal obstruction, 2.0%; Gastroenteritis, 2.0%; and Basal cell carcinoma, 2.0%. The listed terms are not assigned to a specific arm in the record details.

General: adverse-event counts are descriptive. They do not by themselves establish that an event was caused by a study treatment, and comparisons can be affected by event definitions, exposure, and follow-up. The registry record does not provide further detail about event severity beyond serious-event classification, timing, relatedness, or exposure-adjusted rates. These figures should be read as reported safety counts rather than as a complete evaluation of risk.

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

The posted Week 14 results show a higher observed percentage meeting the clinically relevant remission definition in the vedolizumab group than in the placebo group. The sponsor's analysis reports a positive percentage difference, with a 95% confidence interval above zero and p = 0.013. This is evidence of a group difference under the stated analysis, within the trial population and treatment conditions.

The result does not mean that every participant in the vedolizumab group achieved remission, or that no participant in the placebo group did. It does not describe the outcome for a particular individual. The endpoint uses a specific mPDAI threshold and change from Baseline at a specific visit; different definitions, follow-up times, or populations may yield different results. Both groups also received ciprofloxacin up to Week 4, so the randomized contrast is vedolizumab versus matching placebo in the context of that shared regimen.

The confidence interval indicates uncertainty around the estimated group difference, and the arm-specific intervals show uncertainty in the remission percentages. A statistically significant result is not a measure of clinical importance by itself. The record does not provide a threshold for a clinically important between-group difference, and no such threshold should be inferred from the p-value.

The trial's results also do not settle all questions about other outcomes, longer-term effects, safety, or applicability beyond the study population. Secondary findings have varying detail in the registry record, multiplicity handling is not reported, and missing-data methods are not reported. The findings should therefore be understood as the reported randomized comparison on its defined primary endpoint, not as a complete account of every possible outcome or an individual treatment recommendation.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition matters. The primary outcome is not simply a low mPDAI score or improvement from Baseline; it requires both a score below 5 and a reduction of at least 2 points. That compound definition determines which participants count as remitters and shapes the percentages being compared. The endpoint also combines symptom and endoscopic information, making its clinical interpretation different from a single symptom or a continuous score change.

The randomized, masked, placebo-controlled design supports a structured comparison between treatment groups, while the shared ciprofloxacin regimen clarifies what the contrast represents. The result is not a comparison of vedolizumab with no treatment: it is vedolizumab versus matching placebo alongside the listed ciprofloxacin course.

The record also demonstrates the importance of keeping the sponsor's analysis distinct from an unadjusted re-calculation. Both use the posted results, but the reported test and the re-calculated test are not interchangeable. Reporting the effect estimate with its confidence interval gives more information than relying on a p-value alone, while the supplementary calculation can help readers understand the role of analysis choices.

Finally, a positive primary result does not resolve how to interpret numerous secondary analyses. The trial lists multiple outcomes across disease activity, time to remission, and quality of life, yet multiplicity procedures and several analysis details are not reported in the registry record. Separating the primary finding from less fully documented secondary evidence is important for a calibrated statistical reading.

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.

The registry record defines the primary remission outcome and analysis population, but does not report how missing Week 14 observations were handled or provide sensitivity analyses. The influence of missing data on the reported estimate therefore cannot be assessed from these details.

The record lists 9 secondary outcomes and 19 analyses, but does not report a multiplicity adjustment or hierarchy for those analyses. This limits the strength of conclusions that can be drawn from secondary p-values, particularly when detailed estimates are not available for every listed outcome.

For time to PDAI remission, the record provides a hazard ratio and confidence interval but does not report event coding, model specification, or censoring details. Those omissions make independent interpretation of the ratio's direction and assumptions difficult. The record also does not provide detailed allocation procedures or identify which roles were covered by quadruple masking.

The study enrolled 102 participants, and the primary outcome results include 51 participants in each arm. Those figures describe the registry record; they do not establish how much precision was intended by the original design, because the original sample-size justification is not reported. The planning illustrations based on the observed effect cannot substitute for that rationale.

Finally, the primary endpoint is a defined composite threshold at Week 14. It does not capture every dimension of pouchitis or establish whether the same pattern applies at other time points or in populations not described in the record. Further eligibility and generalizability details are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy and Safety of Vedolizumab in the Treatment of Chronic Pouchitis — NCT02790138.
• Registry record last updated 2022-02-24; status last verified 2022-02.
• Results first posted 2021-06-30.
• 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

NCT02790138 is a completed, randomized, double-blind, placebo-controlled Phase 4 parallel-group study of vedolizumab for chronic pouchitis. The registry reports quadruple masking and enrollment of 102. Participants received vedolizumab IV 300 mg or matching placebo, with ciprofloxacin in both groups up to Week 4.

The primary outcome was clinically relevant remission at Week 14, defined using mPDAI score and change from Baseline. The sponsor-reported comparison found a percentage difference of 21.6, with a 95% confidence interval from 4.9 to 37.5 and p = 0.013. The observed remission percentage was higher in the vedolizumab group. The record also lists secondary disease activity, remission, time-to-event, and IBDQ outcomes. Details about multiplicity handling, missing-data methods, and original design assumptions are not reported in the registry record.