Randomized Placebo-Controlled Trial of Budesonide Multi-Matrix System (MMX®) 9 Milligrams (mg) in Participants With Ulcerative Colitis Currently on a 5-Aminosalicylic Acid (5-ASA): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Randomized Placebo-Controlled Trial of Budesonide Multi-Matrix System (MMX®) 9 Milligrams (mg) in Participants With Ulcerative Colitis Currently on a 5-Aminosalicylic Acid (5-ASA) (NCT01532648), a randomized phase 3 study. The primary outcome is Number of Participants Who Achieved Clinical Remission at Day 56.

2. Clinical Question

3. Trial Design

The registry describes a Phase 3, randomized, double-blind, placebo-controlled, parallel-group study. Quadruple masking is recorded, indicating that the masking field includes four roles or parties, although the record does not specify those roles. Random allocation and a parallel-group design mean participants were assigned to one of the comparison groups and remained in that group rather than crossing between treatments.

The trial evaluated budesonide MMX as add-on therapy, not as a replacement for the participants’ existing oral 5-ASA regimen. Participants assigned to budesonide MMX received 9 mg orally for 56 days and continued their existing 5-ASA dose. Participants assigned to placebo received a matching tablet for 56 days and also continued their existing 5-ASA dose. The registry identifies Bausch Health Americas, Inc. as sponsor and records enrollment of 510.

The primary outcome was clinical remission assessed from baseline up to Day 56. The primary analysis population was narrower than the overall enrollment: it consisted of participants who received at least 1 dose, had active ulcerative colitis at study entry as a cause of their symptoms, and had evaluable clinical-remission data. The endpoint description says participants with insufficient Day 56 data were excluded from that analysis.

The registry lists secondary outcomes concerning clinical response, UCDAI remission, endoscopic remission, histologic healing, treatment failure, and quality of life. The posted results include counts for several Day 56 outcomes, but the registry record does not report inferential analyses for those outcomes. The trial is marked completed. Its own original sample-size justification, planned interim analyses, and detailed statistical analysis 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants who received at least 1 dose of study drug and had active ulcerative colitis (UC) at study entry as a cause of their symptoms (Intent-To-Treat Population \[ITT\]) with evaluable clinical remission data.

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: All randomized participants who received at least 1 dose of study drug (Safety Population).

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Who Achieved Clinical Remission at Day 56, measured over Baseline up to Day 56.

The primary endpoint counted participants who achieved clinical remission at Day 56. In this record, remission was defined by two UCDAI components: rectal bleeding and stool frequency. Both component scores had to be 0. This focuses the primary measure on the participant’s reported bleeding and stool frequency symptoms rather than requiring the total UCDAI score to be 0.

The UCDAI is described as the sum of four severity scores, each ranging from 0 to 3, for a total score from 0 to 12. Diary entries were used for stool frequency and rectal bleeding. The endpoint description says the averages for those components were based on 3 days of non-missing diary data closest to Day 56, within 5 days before Day 56. Days involving flexible sigmoidoscopy or colonoscopy, or their preparation, were not included. The averages were rounded to integer values.

This symptom-based definition is used to classify each participant as meeting or not meeting the specified remission criteria at the assessment time. It does not by itself describe every aspect of disease activity or establish durable remission beyond the Day 56 assessment. If a component could not be calculated because of missing data, it was set to missing; participants with insufficient Day 56 data were excluded. Participants already in clinical remission at baseline were classified as non-responders.

7. Results Posted in the Registry

• Budesonide MMX: 24.3% (56/230) versus 22.8% (52/228) on control; risk difference 1.5 percentage points (95% CI -6.2 to 9.3), risk ratio 1.07 (0.77–1.48); unadjusted two-proportion z-test p = 0.698.

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.

Number of Participants of Who Achieved Clinical Response at Day 56

• 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:
  • Budesonide MMX: 43.9% (101/230) versus 37.7% (86/228) on control; risk difference 6.2 percentage points (95% CI -2.8 to 15.2), risk ratio 1.16 (0.93–1.45); unadjusted two-proportion z-test p = 0.178.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Budesonide MMX and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Who Achieved UCDAI Remission at Day 56

• 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:
  • Budesonide MMX: 13.0% (30/230) versus 7.5% (17/228) on control; risk difference 5.6 percentage points (95% CI 0.1 to 11.1), risk ratio 1.75 (0.99–3.08); unadjusted two-proportion z-test p = 0.049.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Budesonide MMX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants Who Achieved Endoscopic Remission at Day 56

• 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:
  • Budesonide MMX: 20.0% (46/230) versus 12.3% (28/228) on control; risk difference 7.7 percentage points (95% CI 1.0 to 14.4), risk ratio 1.63 (1.06–2.51); unadjusted two-proportion z-test p = 0.025.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Budesonide MMX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover several domains: clinical response, UCDAI remission, endoscopic remission, histologic healing, treatment failure, and quality of life. Results are posted for three binary remission or response measures. Across those posted comparisons, the point estimates favor the budesonide MMX group, and the widths and positions of the intervals differ. The registry record does not include posted inferential analyses for the other listed secondary outcomes.

This overall pattern can be considered alongside the primary result, but it does not replace it. The primary endpoint was the prespecified-looking central outcome in the record, with its own definition and analysis population; the secondary measures ask related but not identical questions. Clinical response need not mean full remission, UCDAI remission uses a broader score definition, and endoscopic remission assesses a different domain. Agreement or difference among these measures can reflect their different definitions, measurement methods, and event frequencies.

The secondary comparisons are unadjusted. When several outcomes are examined, the chance of seeing an apparently notable result by chance can increase across the set. Without a reported multiplicity procedure or a stated hierarchy for interpreting these outcomes, secondary p-values and intervals carry less confirmatory weight than a result supported by a prespecified analysis plan. The registry record does not report such a plan or the sponsor’s inferential analyses for the posted secondary outcomes.

Accordingly, the secondary pattern is useful as descriptive context and may inform questions for further study, but it should not be treated as a collection of independent confirmations of the primary finding. These results also do not establish effects on every listed outcome, because several are not accompanied by posted counts or analyses in the registry record.

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

• Number of Participants of Who Achieved Clinical Response at Day 56
• Number of Participants Who Achieved UCDAI Remission at Day 56
• Number of Participants Who Achieved Endoscopic Remission at Day 56
• Number of Participants Who Achieved Histologic Healing at Day 56
• Number of Participants With Treatment Failure at Day 56
• Change From Baseline in Inflammatory Bowel Disease-Quality of Life (IBD-QoL) Questionnaire Scores

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference express?

The primary contrast is a risk difference: the proportion meeting the endpoint in the budesonide MMX group minus the corresponding proportion in the placebo group. A value of zero represents equal proportions. A positive value indicates a larger observed proportion in the budesonide MMX group; a negative value indicates a larger observed proportion in the placebo group. The estimated difference is 0.015, and its interval runs from -0.062 to 0.093. The estimate is an absolute contrast, not a relative increase and not a count of additional participants.

What does the confidence interval contribute?

A confidence interval expresses the uncertainty of an estimate using a range of values compatible with the observed data under the method’s assumptions. It is not a guarantee that the true effect lies in the particular interval, and it does not describe the range of individual participant outcomes. For the primary comparison, the interval includes zero and extends to estimates in both directions. This means the observed data do not give a precise estimate of the direction or magnitude of the group difference.

How should the p-value be read?

The unadjusted p-value for the primary comparison is 0.698. In general, a p-value measures how unusual data at least as discordant with a null hypothesis would be if that null hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the clinical importance of an estimate. The registry record does not report a multiplicity-adjusted primary analysis or a detailed statistical plan. The listed p-value should therefore be understood as an unadjusted comparison, not as a result adjusted for a family of outcomes.

Why do binary outcomes use counts and proportions?

The primary endpoint classifies participants as having achieved remission or not. The arm counts and denominators therefore describe the frequency of an event in each group. A proportion provides a way to compare groups of different sizes, while the count preserves the number of participants represented. The primary analysis denominators are the evaluable groups reported for this outcome; they should not be confused with the overall enrollment or the safety population.

What is the role of the endpoint definition?

The outcome is not simply any improvement in symptoms. It requires a score of 0 for both rectal bleeding and stool frequency. Diary entries nearest to Day 56 were used under the specified rules, and the component averages were rounded to integer values. This makes the endpoint a threshold-based classification: a small change that does not meet both zero-score requirements does not count as remission under this definition. Conversely, meeting the definition indicates that the specified symptom components reached the threshold, but does not imply that every other disease measure was also in remission.

How can missing data affect the comparison?

Missing diary information could prevent calculation of a component score. The record says such a component was set to missing, and participants with insufficient data at Day 56 were excluded from the analysis. It also says baseline remitters were classified as non-responders. These rules affect which observations contribute to the endpoint and how some participants are classified. The record does not report the number of participants excluded for missing data, the detailed missingness pattern, or sensitivity analyses exploring alternative assumptions. Consequently, the posted result cannot establish how the estimate would change under different missing-data approaches.

What is and is not reported about analysis methods?

The registry provides the outcome counts, an unadjusted risk-difference estimate and interval, and an unadjusted p-value. It does not report a detailed model specification, covariate adjustment, a multiplicity procedure, or the trial’s original sample-size justification. The posted results list no reported analyses for the secondary outcomes. These absences mean that additional analytic choices should not be inferred from the summary statistics alone.

For general interpretation, a larger sample can often reduce random uncertainty when the underlying effect and other conditions are held comparable. However, a confidence interval’s width also depends on the event frequency and the analysis method. Statistical precision is not the same as freedom from bias: randomization, missing observations, endpoint measurement, and analysis decisions all matter. The posted primary interval quantifies uncertainty under its calculation, but it cannot answer questions about unreported design or analysis procedures.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.015, with a confidence interval from -0.062 to 0.093. The interval is important because it shows that the point estimate is not precise enough to settle whether the difference favors budesonide MMX, favors placebo, or is close to zero. Its inclusion of zero is consistent with the unadjusted p-value of 0.698, while the range on either side of zero conveys the uncertainty more directly than the point estimate alone.

For a binary endpoint, the observed proportion depends on both the number meeting the definition and the number included in the analysis. The registry reports 56.0 of 230.0 for budesonide MMX and 52.0 of 228.0 for placebo. These denominators reflect the evaluable primary outcome groups, not necessarily all participants enrolled or all participants included in the safety reporting. The endpoint description states that participants with insufficient Day 56 data were excluded.

A confidence interval is not a range of individual responses, and it does not mean that every value in the interval is equally plausible. It is a method-based summary of uncertainty in the estimated group contrast. The interval does not account automatically for all possible sources of uncertainty, such as unreported analysis choices or missing-data mechanisms. Nor does the unadjusted interval address the multiplicity that can arise when several outcomes are examined.

The estimate’s precision is limited: the interval allows both a modest negative and a positive risk difference. The record does not provide an adjusted interval or an inferential analysis for the secondary endpoints. The appropriate reading is therefore cautious and specific to the primary endpoint, its stated population, and the posted calculation.

12. Planning a Similar Trial: Sample Size

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

The planning figures are expressed as participants per arm, not as a total across both arms. They are illustrations based on the observed effect, not the trial’s original design calculations. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. For these non-time-to-event outcomes, the figures are participants per arm; time-to-event planning displays, when applicable, use total events, but that is not the format for these results.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions. The 90% power column uses a higher chance of detection and therefore calls for a larger planning sample for the same effect. These are design-planning quantities, not a description of the probability that the completed trial detected an effect.

The rows labeled for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect show how the illustrative requirement changes when the target effect is smaller than the observed estimate. For example, the primary-outcome illustration gives 11,913 participants per arm for 80% power at 100% of the observed effect, and 47,113 participants per arm for 80% power at 50% of the observed effect. The corresponding 90% power figures are 15,948 and 63,070. Smaller effects need more participants to detect under the same assumptions.

These calculations are not observed power. They do not establish whether the trial was adequately planned, because the original design assumptions and sample-size justification are not reported in the registry record. They are conditional planning illustrations based on the observed estimate, which itself is uncertain.

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 = 0.228; treatment proportion p₁ = 0.243; average p̄ = 0.236.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6003 = 1.1766.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6002 = 0.5051.
4. n = (1.1766 + 0.5051)² / (0.0154)² = 11,912.8, rounded up to 11,913 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.228070175438596                          # control proportion
p1 <- 0.243478260869565                          # 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(1532648)
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 = 11,913 (80% power), 15,948 (90% power)
 75% of observed effect: n per arm = 21,060 (80% power), 28,192 (90% power)
 50% of observed effect: n per arm = 47,113 (80% power), 63,070 (90% power)
power.prop.test: 11912.8 
Simulated power at n = 11,913 per arm: 0.800 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes. Testing or estimating several outcomes raises a multiplicity issue: when many comparisons are considered, some results may look more persuasive by chance alone. A multiplicity procedure or prespecified hierarchy can help define how evidence across outcomes should be interpreted. Such a procedure is not reported in the registry record. The posted secondary comparisons are unadjusted, and the record lists no reported inferential analyses for them. They should therefore be treated as exploratory context rather than as independent confirmatory evidence.

The record reports an unadjusted primary comparison but does not provide a detailed statistical analysis plan, adjusted primary analysis, or interim-analysis information. The registry record does not report the trial’s original sample-size justification or design assumptions. The planning illustrations based on observed effects do not supply those missing design details.

For the primary endpoint, the population was defined as participants who received at least 1 dose, had active ulcerative colitis at entry as a cause of their symptoms, and had evaluable remission data. Participants with insufficient Day 56 data were excluded. When a diary component could not be calculated because of missing data, that component was set to missing. Baseline clinical remitters were classified as non-responders. The registry record does not report the number or pattern of missing observations, reasons for missingness, or sensitivity analyses using other assumptions.

These details matter because the analysis population and missing-data rules affect the observations contributing to an estimate. The posted comparison describes the defined evaluable population under the stated rules; it cannot show whether different missing-data assumptions would produce a similar result. The record also does not provide further detail on how the analysis handled other protocol deviations or on a broader intention-to-treat analysis beyond the endpoint population description.

15. 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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: colitis ulcerative (2.4%), pancreatitis active (0.4%), anemia (0.4%), bronchitis (0.4%), hypokalemia (0.4%).

The safety figures count participants with serious adverse events and participants with other adverse events in groups at risk of 255 for each arm. Serious adverse events affected 10 participants in the budesonide MMX group and 2 in the placebo group. Other adverse events affected 14 participants in each group. These are participant counts, not counts of every event episode; the registry record does not state whether individuals could have experienced more than one event.

The listed serious-event terms include colitis ulcerative at 2.4%, and pancreatitis active, anemia, bronchitis, hypokalemia, and type 2 diabetes mellitus, each at 0.4%. These entries describe reported terms, not proof that study treatment caused them. The safety counts are descriptive and do not by themselves establish comparative risk, particularly without additional detail on event definitions, severity, follow-up, or statistical analysis.

Deaths are not reported in the registry record. Safety group sizes differ from the primary endpoint analysis denominators, so the safety counts should not be combined with or interpreted as if they came from the evaluable efficacy population.

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

The primary result describes a comparison of clinical-remission proportions at Day 56 among the endpoint-evaluable analysis populations. The estimated risk difference was 0.015, with a confidence interval from -0.062 to 0.093 and an unadjusted p-value of 0.698. The interval includes zero and spans estimates in both directions. Thus, the posted primary data do not establish a clear difference between the randomized groups for this specific definition and assessment time.

That conclusion is narrower than saying the treatments are identical. A result that does not provide clear evidence of a difference is not proof of equivalence, and no equivalence margin is reported in the registry record. The uncertainty also means the point estimate should not be treated as a precise measure of the underlying effect. A modest difference in either direction remains compatible with the interval.

The endpoint measures whether participants met a particular symptom threshold: zero scores for rectal bleeding and stool frequency. It does not capture every aspect of ulcerative colitis, establish remission beyond Day 56, or by itself describe long-term outcomes. Participants with insufficient Day 56 data were excluded, and baseline remitters were classified as non-responders. Those endpoint rules define what the reported contrast means.

The study’s add-on comparison concerns budesonide MMX or matching placebo while participants continued their existing oral 5-ASA regimen. It does not answer what would happen with a different background regimen, a different treatment duration, or a different population. The registry record gives counts for several secondary outcomes, but those comparisons are unadjusted and the record does not report inferential analyses for the other listed outcomes. They add descriptive context without overriding the primary result.

The posted safety counts are also descriptive. They show the number of participants with serious and other adverse events in the reported risk groups, but the counts alone cannot attribute events to treatment or establish comparative safety. Overall, the registry results support a careful, endpoint-specific interpretation rather than a broad conclusion about all possible benefits, harms, or clinical circumstances.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be read through its endpoint definition, analysis population, estimate, and uncertainty rather than through the direction of the point estimate alone. The primary risk difference is positive, but its confidence interval includes zero and the unadjusted p-value is 0.698. Those pieces of evidence together show that the observed comparison is not a precise demonstration of a group difference.

It also illustrates how the choice of endpoint shapes the question. Here, clinical remission means zero scores for two symptom components, derived from diary information under specified timing and missing-data rules. It is not interchangeable with total UCDAI remission, endoscopic remission, clinical response, or quality of life. Related outcomes can produce different estimates because they measure distinct aspects of disease activity.

The registry’s secondary outcomes make multiplicity relevant. Without a reported adjustment procedure or analysis hierarchy, a seemingly notable secondary result should be treated with more caution than a result backed by a specified confirmatory plan. The record’s lack of posted inferential analyses for several outcomes further limits what can be concluded across the full outcome set.

Finally, the sample-size illustrations show the importance of planning around a target effect: smaller target effects require more participants under the stated assumptions. Those illustrations are based on the observed effect and are not the trial’s original design justification. Keeping that distinction clear prevents retrospective planning calculations from being mistaken for evidence about the study’s original power or design quality.

18. Limitations

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

The registry record leaves several trial-specific uncertainties. It does not report the original sample-size justification, the planned statistical analysis in detail, interim-analysis plans, or a multiplicity procedure. It also does not provide sponsor-reported inferential analyses for the posted secondary outcomes. These gaps limit assessment of how the reported comparisons relate to the original analysis plan.

The primary endpoint depends on diary entries for rectal bleeding and stool frequency. The record describes how diary observations were selected, rounded, and treated when data were missing, but does not report the extent or pattern of missing diary data, the reasons for missingness, or sensitivity analyses. Excluding participants with insufficient Day 56 information may affect the analysis population, and the available record does not show how alternative assumptions would affect the estimate.

The primary population requires receipt of at least 1 dose and evaluable remission data, rather than simply including everyone enrolled. The registry record does not provide additional detail on the handling of all randomized participants or protocol deviations. The reported primary denominators should therefore be interpreted according to the endpoint-specific population definition.

The secondary results are limited by their unadjusted status and by the absence of posted analysis results for several listed outcomes. Safety reporting gives counts and selected serious-event terms, but the record does not provide a full account of event timing, repeated events, or adjusted comparative safety analyses. Deaths are not reported in the registry record. These limitations do not invalidate the posted figures, but they restrict the strength and scope of conclusions that can be drawn from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Randomized Placebo-Controlled Trial of Budesonide Multi-Matrix System (MMX®) 9 Milligrams (mg) in Participants With Ulcerative Colitis Currently on a 5-Aminosalicylic Acid (5-ASA) — NCT01532648.
• Registry record last updated 2019-09-06; status last verified 2019-08.
• Results first posted 2019-09-06.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed Phase 3 randomized, double-blind, placebo-controlled, parallel-group trial of budesonide MMX 9 mg as add-on therapy for active mild or moderate ulcerative colitis not adequately controlled on oral 5-ASA. The intervention and matching placebo were taken for 56 days while participants continued their existing 5-ASA regimen. Enrollment was 510.

The primary outcome was clinical remission at Day 56, defined as zero scores for rectal bleeding and stool frequency. The posted counts were 56.0 of 230.0 for budesonide MMX and 52.0 of 228.0 for placebo. The risk difference was 0.015, with a confidence interval from -0.062 to 0.093 and an unadjusted p-value of 0.698. The registry record also includes secondary outcome counts and descriptive safety figures, while several analysis-plan details are not reported in the registry record.