Mesalamine 4 g Sachet for the Induction of Remission in Active, Mild to Moderate Ulcerative Colitis (UC): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Mesalamine 4 g Sachet for the Induction of Remission in Active, Mild to Moderate Ulcerative Colitis (UC) (NCT02522767), a randomized phase 3 study. The primary outcome is Proportion of Subjects With Remission.

2. Clinical Question

The result addresses a specific endpoint at a specified assessment time. It is not, by itself, an answer to every question about ulcerative colitis or about outcomes beyond the trial’s follow-up. The registry record does not report a numerical threshold for how large a difference would be important to participants or clinicians.

3. Trial Design

This was a Phase 3, randomized, parallel-group, placebo-controlled study. It enrolled 228 participants with active, mild to moderate ulcerative colitis. The primary comparison assigned 114 participants to mesalamine and 114 to matching placebo. The mesalamine intervention was 4 g extended release granules in a sachet, taken once daily according to the registry description.

The registry lists the study as double-blind in its official title and as quadruple-masked in its design information. Masking is intended to reduce the influence of expectations on care, reporting, and assessment, although the registry record does not specify which groups of people were masked. The record describes a multicenter study and a parallel model, so the two assigned groups were evaluated over the same general trial period rather than being crossed over between treatments.

The primary endpoint was assessed at Week 8. The primary analysis population was the intent-to-treat set, comprising all randomized subjects. The registry lists 15 outcome measures and 8 analyses, and includes several secondary outcomes addressing remission, symptoms, endoscopic findings, and laboratory measures. Numeric results are posted for only some of the secondary outcomes discussed in this analysis.

The trial is marked completed. Its original sample-size justification, planned interim analyses, detailed statistical analysis plan, and specific method for handling missing primary outcome data are not reported in the registry record. The listed planning illustrations are calculations based on observed effects, not documentation of the trial’s original design assumptions.

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: A total of 411 subjects were screened, of which 228 subjects were randomized in a 1:1 ratio to either mesalamine or placebo group (114 subjects each), for 8 weeks double-blind treatment. Subjects who completed 8 weeks but failed to meet the defined criteria for remission received open-label treatment with mesalamine for additional 8 weeks.

Double-blind

Reasons for not completing this period:

Open-label

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT analysis set comprised all randomized subjects.

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: The Intention-to-treat (ITT) analysis set comprised all randomized subjects.

6. Primary Endpoint

The registry lists the primary outcome as Proportion of Subjects With Remission, measured over At Week 8.

The primary endpoint was the proportion of participants with remission at Week 8. The registry defines remission using a Clinical and Endoscopic Response Score: rectal bleeding had to score 0; stool frequency had to score 0 or 1, with at least a 1-point decrease from baseline; and the endoscopic score had to be 0 or 1. The score combines participants’ symptom records with an endoscopic assessment.

The full score ranged from 0 to 9, with higher scores indicating greater disease severity. Its clinical component ranged from 0 to 6 and included stool frequency and rectal bleeding, each scored from 0 to 3 using participants’ daily records. Its endoscopic component ranged from 0 to 3 and was based on flexible sigmoidoscopy or colonoscopy. The endpoint therefore represents a combined criterion rather than a single symptom or an endoscopic finding alone.

A binary remission outcome is useful for expressing how many participants met a prespecified clinical and endoscopic definition by a particular assessment time. It makes the groups’ observed event counts directly interpretable. At the same time, reducing several measures to whether a participant meets the threshold does not show the full range of symptom or endoscopic changes. The registry record does not report additional information about the clinical importance threshold for this endpoint.

7. Results Posted in the Registry

• Mesalamine: 16.7% (19/114) versus 11.4% (13/114) on control; risk difference 5.3 percentage points (95% CI -3.7 to 14.3), risk ratio 1.46 (0.76–2.82); unadjusted two-proportion z-test p = 0.253.

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.

Proportion of Subjects With Remission in the Primary Endpoint and the Physician's Global Assessment (PGA) Score of ≤1 (Modified Mayo Score)

• 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:
  • Mesalamine: 16.7% (19/114) versus 9.6% (11/114) on control; risk difference 7.0 percentage points (95% CI -1.7 to 15.7), risk ratio 1.73 (0.86–3.46); unadjusted two-proportion z-test p = 0.117.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Mesalamine and the control. The interval gives the range of effects that remain compatible with the data.

The Proportion of Subjects With Endoscopic Improvement

• 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:
  • Mesalamine: 29.8% (34/114) versus 19.3% (22/114) on control; risk difference 10.5 percentage points (95% CI -0.6 to 21.6), risk ratio 1.55 (0.97–2.47); unadjusted two-proportion z-test p = 0.065.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Mesalamine and the control. The interval gives the range of effects that remain compatible with the data.

Time to Normal Stool Pattern

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Mesalamine vs Placebo: hazard ratio 1.36 (95% CI 0.91–2.02), reported p > 0.050 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Mesalamine vs Placebo and the control. The interval gives the range of effects that remain compatible with the data.

The numeric secondary comparisons have point estimates that generally lean in the same direction as the primary point estimate: the posted binary outcomes have more events in the mesalamine arm, and the time-to-event comparison has a hazard-ratio estimate above 1. The confidence intervals for these comparisons include the respective no-difference values, and the reported tests do not show a statistically clear separation. Taken together, this pattern is directionally consistent but does not provide precise confirmation of the primary result.

These measures address different aspects of the trial. The secondary outcomes include a stricter remission definition incorporating the Physician’s Global Assessment, endoscopic improvement, and time to normal stool pattern. The registry also lists outcomes relating to rectal bleeding, clinical remission at multiple assessments, C-reactive protein, and fecal calprotectin. Those outcomes can help characterize symptoms, endoscopic status, and laboratory measures, but they are not interchangeable with the primary composite endpoint.

The registry record lists multiple outcome measures, and the posted material does not report a multiplicity adjustment for the secondary analyses. General explanation: when many outcomes are examined, the chance of at least one apparently notable result arising by chance can increase. Adjustments or a prespecified hierarchy can help address that issue, but whether such procedures were used is not reported in the registry record.

Accordingly, secondary results are best read as supporting context rather than independent proof. The broad directional pattern is informative, but uncertainty and multiple testing limit the weight that should be assigned to isolated secondary findings. Numeric results for every listed secondary outcome are not reported in the registry record.

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

• Proportion of Subjects With Remission in the Primary Endpoint and the Physician's Global Assessment (PGA) Score of ≤1 (Modified Mayo Score)
• Time to Cessation of Rectal Bleeding
• The Proportion of Subjects With Endoscopic Improvement
• The Proportion of Subjects in Clinical Remission at Weeks 2, 4, and 8
• Time to Normal Stool Pattern
• The Change From Baseline in Rectal Bleeding Score at Weeks 2, 4, and 8
• The Change From Baseline in Serum C-reactive Protein (CRP) Levels at Weeks 2, 4, and 8
• The Change From Baseline in Fecal Calprotectin Levels at Week 8

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

A risk difference is the difference between the observed proportions of participants meeting an outcome in two groups. It is expressed on the probability scale, rather than as a ratio. For the primary endpoint, the posted estimate is 0.053 for mesalamine compared with placebo. The confidence interval runs from -0.037 to 0.142. Negative values would indicate a lower remission proportion in the mesalamine group; positive values would indicate a higher proportion. Because the interval covers zero, the data do not rule out no difference at the confidence level used.

General explanation: absolute differences are often easier to connect to the observed proportions than relative measures, but they can depend strongly on the outcome frequency in the population being studied. They also do not, on their own, indicate whether a difference is important in practice. The registry record does not state a threshold for clinical importance.

What does an odds ratio add?

The sponsor’s primary analysis reports an odds ratio. An odds ratio compares the odds of the outcome in one group with the odds in the other; it is not the same quantity as a risk ratio or a risk difference. The reported estimate is 1.55, with a 95% confidence interval from 0.73 to 3.32. An odds ratio of 1 represents equal odds. Because the interval includes 1, the reported result does not establish a statistically clear difference by this measure.

General explanation: odds and probabilities are related but are not interchangeable. For common outcomes, an odds ratio can look farther from 1 than the corresponding risk ratio. It is therefore useful to retain the measure’s name and avoid translating an odds ratio directly into a percentage increase in probability.

How should the p-value be read?

The sponsor reports p >0.05 for the primary comparison, while the unadjusted recalculation from the posted counts gives p=0.253. A p-value describes how compatible the observed data are with a specified null model, 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 importance of an effect. A result above a conventional threshold is not proof of no effect. The estimate and its confidence interval remain important for understanding the range of effects compatible with the data.

General explanation: a chi-squared test assesses whether observed counts differ from counts expected under a null hypothesis of no association. The registry identifies a chi-squared method for the sponsor’s reported odds-ratio analysis. The registry record does not report further details of the test implementation.

What does the time-to-event analysis measure?

One secondary outcome concerns time to normal stool pattern, assessed up to Week 8. The mesalamine median is 55 days, with the lower confidence limit reported as 35 days; the placebo median is not reported. The comparison reports a hazard ratio of 1.36, with a 95% confidence interval from 0.91 to 2.02, using a log-rank method. The reported p-value is p >0.05.

General explanation: a median time is the time by which half of the relevant group has experienced the event, if that point can be estimated. A hazard ratio compares the event rates over follow-up under a time-to-event model. Its interpretation depends on how the event and direction are defined; the registry record does not explain the coding details or report a proportional-hazards assessment. The log-rank method compares event-time patterns between groups while accounting for the timing of events, rather than treating every participant as if follow-up ended at the same event time.

Why do intervals matter?

A confidence interval displays uncertainty around an estimate under the method used to calculate it. Wider intervals indicate less precision; intervals that include the null value allow a range of possibilities that includes no difference. The primary risk-difference interval includes zero, and the sponsor’s odds-ratio interval includes 1. Those features are consistent with the reported lack of statistical significance. General explanation: confidence intervals are not guarantees that a particular interval contains the true effect, nor do they incorporate every possible source of bias or design limitation.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.053, with a 95% confidence interval from -0.037 to 0.142. The interval includes zero and extends across both negative and positive values. This means the posted data do not precisely distinguish no difference from a range of possible group differences. The point estimate alone is not an adequate summary of that uncertainty.

The sponsor-reported odds ratio is 1.55, with a 95% confidence interval from 0.73 to 3.32. Since an odds ratio of 1 represents equal odds, the interval is compatible with lower odds as well as higher odds in the mesalamine arm. The interval is broad relative to the point estimate, so the magnitude and direction of the underlying association remain uncertain.

Confidence intervals describe statistical uncertainty under the analysis method; they do not account automatically for possible limitations in measurement, missing data, analysis choices, or generalizability. The registry record does not report enough detail to assess all those issues. The number of participants in each arm and the observed event counts are relevant to precision, but a confidence interval is the more direct guide to the range of values compatible with the analysis.

General explanation: a confidence interval is not a range containing 95% of individual participant outcomes, and it is not a probability statement about the fixed true effect. It is a method-based interval that would have a stated long-run coverage property if the underlying assumptions held across repeated studies.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning illustrations are based on the observed effect, not on the trial’s original design. For the binary outcomes, the figures are participants per arm. For the time-to-event outcome, they are total events, not participants per arm. The calculations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The time-to-event illustrations use the Schoenfeld approach.

The 80% power column gives the planning size associated with an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one and the model assumptions held. The 90% power column uses a higher target chance of detecting the same specified effect, and consequently generally requires more information. These are design-planning concepts, not probabilities that the observed result is true.

For the primary comparison, the illustration based on 100% of the observed effect gives 683 participants per arm for 80% power and 914 participants per arm for 90% power. Planning for 75% of the observed effect gives 1,167 participants per arm for 80% power and 1,561 participants per arm for 90% power. Planning for 50% of the observed effect requires still more participants per arm. The sample-size curve expresses the same general relationship: smaller effects are harder to distinguish from random variation and therefore require more participants or events.

These figures are planning illustrations based on the observed effect, not observed power. They do not establish what the trial was originally designed to detect. The trial’s original sample-size assumptions are not reported in the registry record.

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 = 0.114; treatment proportion p₁ = 0.167; average p̄ = 0.140.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4912 = 0.9628.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4898 = 0.4122.
4. n = (0.9628 + 0.4122)² / (0.0526)² = 682.5, rounded up to 683 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 <- 0.114035087719298                          # control proportion
p1 <- 0.166666666666667                          # 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(2522767)
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 = 683 (80% power), 914 (90% power)
 75% of observed effect: n per arm = 1,167 (80% power), 1,561 (90% power)
 50% of observed effect: n per arm = 2,516 (80% power), 3,367 (90% power)
power.prop.test: 682.5 
Simulated power at n = 683 per arm: 0.802 (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 an odds ratio of 1.55, with a 95% confidence interval from 0.73 to 3.32 and p >0.05, using a chi-squared method. The recalculation from the posted group counts gives an odds ratio of 1.554, with a confidence interval from 0.727 to 3.319 and an unadjusted p-value of 0.253. These odds-ratio estimates and intervals are numerically close, although their displayed precision differs.

The recalculation also expresses the primary comparison as a risk difference: 0.053, with a 95% confidence interval from -0.037 to 0.142. This is a separate, unadjusted expression of the comparison, not a replacement for the sponsor’s analysis. Different measures answer related but distinct questions, so their numeric values should not be compared as though they were on the same scale.

The registry record does not report additional details that would allow a full reconstruction of the sponsor’s analysis. The sponsor-reported estimate and test should therefore be treated as the trial’s own posted analysis, while recalculated values are useful supplementary descriptions of the posted counts.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies the intent-to-treat analysis population for the primary endpoint as all randomized subjects. This definition is important because it retains participants in the groups to which they were randomized, which preserves the basis for the randomized comparison. The primary arm counts are 114 participants each.

The record lists numerous outcome measures and analyses, but does not report whether the primary outcome was tested within a prespecified hierarchy or whether any adjustment was made for multiple comparisons. General explanation: testing many outcomes can increase the chance of a false-positive finding if each is judged separately using the same threshold. A multiplicity strategy may control that risk, but the record does not describe one, so it is not possible to determine how secondary tests were intended to be interpreted collectively.

The registry record does not report the amount or pattern of missing primary endpoint data, the method used to handle missing values, or sensitivity analyses addressing missingness. It also does not report the detailed statistical analysis plan, including any per-protocol population or rules for deviations from assigned treatment. The stated ITT population alone does not establish how participants without an observed endpoint were handled.

These omissions do not invalidate the posted results, but they limit independent assessment of potential bias from missing information and of the planned status of the analyses. They also make it harder to distinguish confirmatory outcomes from exploratory ones. The registry record does not report whether interim analyses were planned or conducted, so no assumption about interim monitoring should be made.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: tracheitis (0.9%), appendicitis (0.6%), spondylitis (0.6%).

For the randomized comparison, the registry reports 1 serious adverse event among 114 participants in the mesalamine group and 0 among 114 participants in the placebo group. It reports 19 other adverse events in the mesalamine arm and 13 in the placebo arm. No deaths are reported in either randomized arm.

The registry also lists an open-label mesalamine group with 170 participants, 2 serious adverse events, 8 other adverse events, and 0 deaths. That group is not the randomized placebo comparison and should not be combined with the randomized mesalamine arm to interpret the treatment contrast. The listed serious adverse event terms include tracheitis at 0.9%, appendicitis at 0.6%, and spondylitis at 0.6%.

These are counts reported in the registry, not adjusted comparisons of safety risk. The registry record does not provide enough detail to assess event timing, duration, relatedness, or statistical uncertainty for the safety outcomes. The counts should therefore be read descriptively and in the context of the recorded group sizes, without treating them as a complete account of safety.

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

The result describes the proportion meeting a defined clinical and endoscopic remission criterion at Week 8 among randomized participants assigned to mesalamine or placebo. The observed counts were 19 of 114 and 13 of 114, respectively. The risk-difference estimate favors a higher observed remission proportion in the mesalamine arm, but its confidence interval includes zero and spans negative and positive values. The sponsor’s odds-ratio analysis likewise has a confidence interval that includes the no-association value and reports p >0.05.

These findings do not establish a statistically clear difference between the groups, but they also do not demonstrate that the groups are equivalent. An absence of statistical significance can reflect uncertainty as well as a small or absent effect. The intervals indicate that the posted data are compatible with multiple possible effect sizes and directions.

The result is specific to the registry’s endpoint definition, the Week 8 assessment, and the participants represented in the ITT analysis set. It does not answer whether other outcomes differ, whether effects persist beyond the reported follow-up, or whether the same estimates apply to populations not represented in the trial. The registry record does not report a clinical importance threshold, a detailed missing-data strategy, or all statistical planning details.

No medical conclusion should be drawn from the statistical result alone. The estimates describe the posted trial data and their uncertainty; they do not establish the overall balance of benefits and harms or determine a course of care.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should be read through both its estimate and its uncertainty. The primary point estimate is positive on the risk-difference scale, but the confidence interval crosses zero. The sponsor’s odds-ratio interval also crosses its null value. Reporting only the direction of the point estimate would miss the substantial uncertainty in the comparison.

It also shows why effect measures matter. An odds ratio, risk difference, and time-to-event hazard ratio summarize different features of data and are not interchangeable. The same trial can report the sponsor’s odds-ratio analysis while a simple recalculation describes the absolute difference in observed proportions. Both can be informative when clearly identified and interpreted on their own scales.

The secondary outcomes add breadth but raise the issue of multiplicity. A collection of endpoint results can reveal whether a pattern is broadly consistent, yet repeated testing can make isolated findings harder to interpret. Without a reported multiplicity strategy, secondary outcomes are appropriately treated as contextual rather than as decisive evidence on their own.

Finally, planning illustrations based on the observed effect help explain the relationship between effect size and required information, but they cannot recover the trial’s original design rationale. The registry record does not report that rationale. Separating observed results, sponsor analyses, recalculations, and hypothetical planning scenarios is essential for a transparent 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.

The primary comparison is based on 114 participants in each arm, and the number meeting the remission criterion was limited in both groups. The resulting confidence interval is broad and includes the no-difference value. Consequently, the point estimate should not be treated as a precise estimate of the underlying effect.

The registry record does not report how missing primary outcome data were handled, how many participants lacked an endpoint assessment, or whether sensitivity analyses were conducted. It also does not report a detailed statistical analysis plan, the original sample-size assumptions, or whether interim analyses took place. These are important limits on evaluating the analysis against the planned protocol.

Multiple outcomes are listed, while a multiplicity strategy is not reported. This makes secondary results more difficult to interpret as confirmatory evidence. Numeric results are not reported in the registry record for every listed secondary outcome. The secondary findings that are posted therefore cannot establish a complete picture across all outcomes.

The trial’s follow-up for the primary outcome is specified at Week 8. The registry record does not establish the durability of the endpoint beyond that assessment. Safety information is presented as event counts and does not include enough detail to assess timing, severity beyond the serious-event classification, relatedness, or comparative uncertainty. These limitations call for a restrained description of what the registry results can establish.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Mesalamine 4 g Sachet for the Induction of Remission in Active, Mild to Moderate Ulcerative Colitis (UC) — NCT02522767.
• Registry record last updated 2021-03-15; status last verified 2021-02.
• Results first posted 2021-03-15.
• 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 record describes a completed, randomized, double-blind, placebo-controlled, multicenter Phase 3 study of mesalamine 4 g extended release granules in participants with active, mild to moderate ulcerative colitis. The primary comparison included 114 participants assigned to mesalamine and 114 assigned to matching placebo.

At Week 8, remission was recorded for 19 participants in the mesalamine group and 13 in the placebo group. The posted risk difference is 0.053, with a 95% confidence interval from -0.037 to 0.142. The sponsor reports an odds ratio of 1.55, with a 95% confidence interval from 0.73 to 3.32 and p >0.05. Both estimates leave substantial uncertainty about the difference between groups.

The registry also reports secondary outcomes and descriptive safety counts. The original sample-size justification, missing-data handling, detailed statistical plan, and multiplicity approach are not reported in the registry record.