Efficacy and Safety of Budesonide Foam for Participants With Active Mild to Moderate Ulcerative Proctitis or Proctosigmoiditis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Budesonide Foam for Participants With Active Mild to Moderate Ulcerative Proctitis or Proctosigmoiditis (NCT01008410), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Achieved Remission.

2. Clinical Question

The study addresses a short-term, treatment-versus-placebo question in people with active disease of specified mild to moderate severity and location. It does not ask whether the groups differed on every aspect of disease activity, nor does remission mean that every participant had a score of 0 on every MMDAI component. It is a composite endpoint: a participant had to satisfy the stated endoscopy, rectal bleeding, and stool-frequency criteria together.

The registry record describes a randomized, double-blind, placebo-controlled study and lists 265 participants as enrolled. The treatment period in the stated dosing schedule runs through week 6, which is also the primary endpoint time. The registry record does not report results beyond the listed assessment time, so the primary comparison is a week-6 result rather than evidence about longer-term outcomes.

3. Trial Design

This was a phase 3, randomized, triple-masked, parallel-group, placebo-controlled study. Participants were assigned to rectal budesonide foam or matching placebo. The registry record lists 265 participants as enrolled; the primary outcome results include 133 participants in the budesonide group and 132 in the placebo group. The study is marked completed. Its start date is 2009-11-17 and its primary completion date is 2013-04-29.

The treatment schedule began with twice-daily dosing for 2 weeks and continued with once-daily dosing for 4 weeks. Budesonide was given as 2 mg/25 mL foam. The placebo group received 25 mL of matching foam on the corresponding schedule. Participants could continue established oral 5-aminosalicylic acid treatment at doses up to 4.8 grams/day. The registry record does not report whether other background treatments were permitted or how their use was handled analytically.

Random allocation is intended to make treatment groups comparable, on average, with respect to both measured and unmeasured characteristics. Masking is intended to limit effects of treatment knowledge on participant experience, clinical assessment, and conduct of the study. The registry record identifies triple masking but does not specify which roles were masked. A parallel-group design assigns each participant to one study group rather than having participants cross between treatments.

The registry record does not report the original sample-size justification, allocation ratio details beyond the group counts, randomization procedure, exact masking roles, or planned interim analyses. The posted primary analysis used the intention-to-treat population and last observation carried forward for missing data. Details of additional protocol deviations, participant flow, and the amount or timing of missing outcome data 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: ITT population included all randomized participants. Missing data was imputed using last observation carried forward (LOCF) method.

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: Intent-to-treat (ITT) population included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Achieved Remission, measured over Week 6.

The primary endpoint was the percentage of participants who achieved remission at week 6. Remission combined clinical and endoscopic findings using the Modified Mayo Disease Activity Index (MMDAI). Participants met the definition if the endoscopy score was at most 1, rectal bleeding was scored 0, and stool frequency had improved or had not worsened from baseline. Because all these conditions were required together, the endpoint represents a combined outcome rather than a result on any single MMDAI component.

The MMDAI assessed stool frequency, rectal bleeding, physician's global assessment, and endoscopy. Each index was scored from 0 to 3, for a maximum total score of 12. For stool frequency, 0 indicated a normal number of stools per day and 3 indicated 5 or more stools than normal. For rectal bleeding, 0 indicated no blood seen and 3 indicated blood alone passed. For endoscopy, 0 indicated normal or inactive disease and 3 indicated severe disease, including spontaneous bleeding or ulceration.

A combined endpoint is used to capture more than one dimension of disease activity in a single outcome. It can make the result clinically interpretable as a defined state, but it also means a participant can fail to meet remission if any required component does not satisfy its criterion. The registry record does not report separate primary estimates for each component within the remission definition.

7. Results Posted in the Registry

• Budesonide: 38.3% (51/133) versus 25.8% (34/132) on control; risk difference 12.6 percentage points (95% CI 1.5 to 23.7), risk ratio 1.49 (1.04–2.14); unadjusted two-proportion z-test p = 0.028.

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 Who Achieved a Rectal Bleeding MMDAI Subscale Score of 0 at End of Week 6

• 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:
  • Budesonide: 46.6% (62/133) versus 28.0% (37/132) on control; risk difference 18.6 percentage points (95% CI 7.2 to 30.0), risk ratio 1.66 (1.20–2.31); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Budesonide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Who Achieved an Endoscopy MMDAI Subscale Score of 0 or 1 at End of Week 6

• 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:
  • Budesonide: 55.6% (74/133) versus 43.2% (57/132) on control; risk difference 12.5 percentage points (95% CI 0.5 to 24.4), risk ratio 1.29 (1.01–1.65); 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 Budesonide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Who Achieved a Score of 0 for Rectal Bleeding Subscale and a Combined Score of <=2 for Bowel Frequency and Physician's Global Assessment (PGA) in the MMDAI Subscales at End of Week 6

• 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:
  • Budesonide: 41.4% (55/133) versus 25.8% (34/132) on control; risk difference 15.6 percentage points (95% CI 4.4 to 26.8), risk ratio 1.61 (1.13–2.29); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Budesonide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted numerical results for the secondary outcomes move in the same direction as the primary result: the reported percentages favor budesonide on rectal bleeding, endoscopy, and a combined threshold involving rectal bleeding, bowel frequency, and physician's global assessment. These endpoints are related to the clinical and endoscopic dimensions incorporated into the primary remission definition. Their directional consistency offers context for the primary finding, but it does not make them independent confirmations, because the outcomes overlap conceptually and draw on the same trial population and assessment period.

The registry record lists 9 secondary outcomes, while numerical group comparisons are reported for three of them in the record details. Results for the other listed secondary outcomes are not reported in the registry record. The numerical secondary comparisons are unadjusted, and the record does not describe a multiplicity correction or a hierarchy that would specify how these tests should be interpreted relative to one another.

General statistical context: when many outcomes are examined, the chance of seeing at least one apparently notable result can increase, even if all comparisons reflect no underlying difference. Adjustment procedures or prespecified testing sequences can address this issue, but the record does not report whether either was used for the secondary outcomes. An unadjusted secondary p-value therefore carries less evidential weight than a single prespecified primary comparison interpreted under its analysis plan. It is better viewed as supportive or exploratory context rather than as a stand-alone confirmatory conclusion.

The secondary results also cannot establish the separate contribution of each part of remission or demonstrate that every dimension improved in every participant. They are proportions meeting specific criteria at week 6. The registry record does not provide participant-level relationships among the outcomes, subgroup results, or longer-term assessments. The overall pattern is consistent in direction across the numerical secondary comparisons, but its scope remains limited by outcome overlap, multiplicity information not reported in the registry record, and the available follow-up.

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

• Percentage of Participants Who Achieved a Rectal Bleeding MMDAI Subscale Score of 0 at End of Week 6
• Number of Scheduled Assessments With Rectal Bleeding Responder Classification
• Percentage of Participants Who Achieved an Endoscopy MMDAI Subscale Score of 0 or 1 at End of Week 6
• Percentage of Participants Who Achieved a Score of 0 for Rectal Bleeding Subscale and a Combined Score of <=2 for Bowel Frequency and Physician's Global Assessment (PGA) in the MMDAI Subscales at End of Week 6
• Percentage of Participants Who Achieved an MMDAI Total Score of <= 3 With Greater Than or Equal to (>=2) Points of Improvement From Baseline at the End of Week 6
• Percentage of Participants Who Achieved Improvement of >=1 Point From Baseline in the MMDAI Endoscopy Subscale Score at End of Week 6
• Percentage of Participants Who Achieved Improvement of >=1 Point From Baseline in the MMDAI Rectal Bleeding Subscale Score at End of Week 6
• Percentage of Participants Who Achieved >=3 Point Improvement From Baseline in the MMDAI Total Score Including Improvement of >=1 Point From Baseline in the MMDAI Rectal Bleeding Subscale Score and MMDAI Endoscopy Subscale at End of Week 6

9. Statistical Interpretation

10. Statistical Methods Explained

What kind of outcome is remission? The primary endpoint is binary at the participant level: each participant either met the remission definition at week 6 or did not. The reported arm values are percentages, so the central comparison is between two proportions. For a binary endpoint, a risk difference expresses the absolute contrast between those proportions. The recalculated risk difference is 0.126. Its reported interval runs from 0.015 to 0.237. These are unadjusted summary-statistic calculations, not the sponsor's regression estimate.

Why use a combined endpoint? General statistical context: a composite endpoint can represent several clinically relevant dimensions in one outcome and avoids reducing the question to a single symptom or examination finding. Its interpretation depends on the exact rule. In this trial, remission required an endoscopy score at most 1, no rectal bleeding, and stool frequency that improved or did not worsen. A participant had to satisfy all three requirements. The percentage meeting this joint rule therefore does not show the separate contribution of each component.

What does the risk difference say? General statistical context: the risk difference subtracts one group's event proportion from the other's, with the direction determined by the comparison convention. It is an absolute contrast, rather than a relative measure. The posted recalculation reports 0.126, with interval limits 0.015 and 0.237. The group percentages are 38.3% and 25.8%, respectively. No additional percentage-point value is calculated. The registry record also lists recalculated relative measures, but these do not replace the absolute comparison and are not the sponsor's reported regression result.

What does the p-value represent? General statistical context: a p-value measures how unusual data at least as discrepant as the observed data would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor a measure of the size or practical importance of a difference. The sponsor's reported logistic regression analysis gives p = 0.032. The unadjusted recalculation gives p = 0.028. The registry record does not provide the model specification or covariates needed to reconstruct the sponsor's regression analysis. The two p-values should therefore be kept distinct rather than treated as interchangeable outputs from one method.

Why can model choice matter? General statistical context: logistic regression models the odds of a binary outcome and can account for specified covariates. An unadjusted comparison uses only the group-level event information in the posted summaries. Adjusted and unadjusted estimates can differ because they use different information and assumptions. The registry record identifies logistic regression for the sponsor's analysis but does not state whether covariates were included. The recalculated results are explicitly unadjusted. The record marks discrepancy as false, so the posted recalculation is not identified as conflicting with the sponsor's result.

How should interval estimates be read? General statistical context: a confidence interval is a range of estimates compatible with the observed data under a particular method and its assumptions. Its width conveys precision: a narrower range indicates less sampling uncertainty than a wider range on the same scale. The risk-difference interval is reported as 0.015 to 0.237. The registry record does not state the confidence level or the interval-construction method for this recalculation, so neither should be inferred. An interval is not a guarantee that the true effect lies within its limits, and it does not incorporate all possible sources of bias or design uncertainty.

How does the analysis population affect interpretation? The primary population is described as intention-to-treat and includes all randomized participants. The record says missing data were imputed by last observation carried forward (LOCF). In general, LOCF carries a participant's last observed outcome forward to a later assessment when the later value is missing. This is an assumption about the unobserved outcome, not an observed measurement. Its implications depend on why data are missing and how outcomes change over time. The record does not report the number of missing week-6 values, reasons for missingness, or sensitivity analyses using alternative assumptions.

Why does over-dispersion matter in some analyses? General statistical context: over-dispersion arises when variability exceeds what a statistical model assumes, and can lead to uncertainty estimates that are too small if ignored. It is relevant to some count and rate models, but the primary endpoint is binary, and the registry record identifies logistic regression for the sponsor's analysis. No over-dispersion analysis is reported for this endpoint. It would be inappropriate to assume that such a model issue was examined or to import it as a feature of the posted analysis.

What is the role of the secondary outcomes? Secondary endpoints examine related measures, including rectal bleeding, endoscopy, and other MMDAI criteria. General statistical context: examining multiple outcomes creates more opportunities for apparently unusual findings, even when no true difference exists on any outcome. A prespecified multiplicity plan can control or organize interpretation of that issue. The registry record does not report such a plan. The primary endpoint should therefore remain distinct from unadjusted secondary comparisons, which are less definitive when considered as a family of tests.

11. Confidence Intervals and Precision

The recalculated risk difference for week-6 remission is 0.126, with reported interval limits of 0.015 and 0.237. The interval is entirely on the positive side of 0, but its range spans effects of different sizes. This supports a directionally positive unadjusted estimate while leaving uncertainty about its magnitude. The registry record does not state the interval's confidence level or construction method, so the limits should be read as the reported interval rather than assigned an unstated level.

Precision is distinct from the observed group percentages. The percentages, 38.3% for budesonide and 25.8% for placebo, are sample estimates. The interval conveys sampling uncertainty around the recalculated contrast, not certainty about each participant's outcome and not a measure of clinical importance. A relatively wide interval can include materially different effect sizes; it does not mean the result is invalid, but it limits how precisely the difference can be stated.

The sponsor's analysis reports p = 0.032 from logistic regression, while the unadjusted recalculation reports p = 0.028. The record does not report a regression estimate or its interval, which prevents a direct comparison of precision between the sponsor's model and the unadjusted risk difference. The analysis methods differ, and the sponsor's p-value alone does not show the range of effect sizes compatible with that model.

Intervals reflect statistical uncertainty under an analysis and its assumptions. They do not account automatically for issues such as missing-data assumptions, endpoint selection, multiplicity, or departures from the study population of interest. In this trial, the primary analysis used LOCF for missing data, and the record does not report the extent of missingness or sensitivity analyses. Those omissions limit assessment of how robust the precision estimate is to alternative assumptions.

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 participants per arm, not total events. The planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers effects defined as a stated fraction of the observed effect. The original trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a hypothetical future study to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and those assumptions were correct. The 90% power column expresses the corresponding planning target for a 90% chance. These are design illustrations, not guarantees about a future study's result. For the primary endpoint, planning for 100% of the observed effect gives 215 participants per arm for 80% power and 287 participants per arm for 90% power. Planning for 75% of the observed effect gives 372 and 498 participants per arm, respectively; planning for 50% gives 814 and 1,089.

Smaller effects are harder to distinguish from random variation, so the planning figures rise as the assumed effect is reduced. This relationship is a general feature of study planning: if a future study aims to detect a more modest difference while retaining the same stated power and significance level, it generally needs more participants. The curve represents that planning relationship; its values depend on the assumptions used and should not be treated as trial observations.

These figures are not observed power. They are forward-looking planning illustrations based on the observed effect and stated assumptions, not a retrospective measure of how successful the completed trial was. They also do not recover the rationale used to design the original trial, which is 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 = 0.258; treatment proportion p₁ = 0.383; average p̄ = 0.321.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6600 = 1.2935.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6539 = 0.5504.
4. n = (1.2935 + 0.5504)² / (0.1259)² = 214.6, rounded up to 215 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 <- 0.257575757575758                          # control proportion
p1 <- 0.383458646616541                          # 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(1008410)
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 = 215 (80% power), 287 (90% power)
 75% of observed effect: n per arm = 372 (80% power), 498 (90% power)
 50% of observed effect: n per arm = 814 (80% power), 1,089 (90% power)
power.prop.test: 214.6 
Simulated power at n = 215 per arm: 0.803 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry record reports the sponsor's primary comparison as logistic regression, with p = 0.032. It does not report the model coefficient, adjusted effect estimate, confidence interval, covariates, or further details of the model. The sponsor's result is therefore best described as the reported model-based test, without inferring an adjusted risk difference or a model specification that is not stated.

The recalculated comparison uses the posted group summaries and is unadjusted. It gives a risk difference of 0.126, with interval limits of 0.015 and 0.237, and p = 0.028. The recalculation is useful as a transparent comparison of the reported proportions, but it answers a more limited statistical question than a regression analysis that may incorporate additional information. The registry record does not identify a discrepancy between the sponsor's result and the recalculation.

Accordingly, the two p-values should not be substituted for one another or treated as competing estimates from identical methods. The sponsor's own analysis is the trial's reported analysis; the recalculation is an unadjusted check derived from the group summaries. Neither p-value conveys the size of the effect by itself. The unadjusted risk difference and its interval provide an effect-scale description, while the sponsor's p-value reports the result of the stated regression test.

15. Multiplicity, Missing Data and Analysis Populations

The record lists a primary endpoint and 9 secondary outcomes. It reports one sponsor analysis for the primary comparison and unadjusted recalculated comparisons for the primary endpoint and selected secondary endpoints. The registry record does not report a multiplicity adjustment, a gatekeeping procedure, or a prespecified hierarchy for testing the secondary outcomes. It also does not state whether the primary test was protected from other analyses by a planned testing strategy.

General statistical context: testing multiple outcomes can increase the probability of obtaining a small p-value by chance somewhere among the tests. A multiplicity plan can control the overall error rate or define which comparisons are confirmatory. Without information about such a plan, individual unadjusted secondary results should be interpreted cautiously and should not be treated as equivalent to the primary result. The primary result also should be understood in the context of its stated endpoint definition and analysis method, not as a blanket conclusion about every registered outcome.

The primary analysis population is described as intention-to-treat, including all randomized participants. The primary endpoint description says missing data were imputed using last observation carried forward (LOCF). LOCF uses a participant's last recorded observation as the value carried to a later missing assessment. This method makes an assumption about the unobserved week-6 result; the imputed value is not an observed week-6 measurement.

The registry record does not report how many participants had missing primary outcome data, reasons for missingness, timing of the last observed values, or sensitivity analyses under alternative missing-data assumptions. It does not report whether all secondary analyses used the same population or imputation method. These gaps limit evaluation of the effect of missing data and the consistency of the analysis populations. The record also does not report the original sample-size justification, interim analyses, or a detailed statistical analysis plan. Those elements cannot be inferred from the posted results.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: ectopic pregnancy (1.2%), anaemia (0.8%), colitis ulcerative (0.8%), hypersensitivity (0.7%), arterial thrombosis limb (0.7%).

The posted safety counts describe participants at risk and participants affected, not event rates calculated. Serious adverse events affected 2 participants among 134 at risk in the budesonide group and 3 among 131 at risk in the placebo group. Other adverse events affected 66 of 134 participants at risk in the budesonide group and 47 of 131 at risk in the placebo group. The registry record reports 0 deaths in each group.

These counts are descriptive. They do not establish that an event was caused by study treatment, and the registry record does not provide event-level timing, severity, duration, or treatment attribution for each participant. The listed serious adverse event terms include ectopic pregnancy at 1.2%, anaemia at 0.8%, colitis ulcerative at 0.8%, hypersensitivity at 0.7%, and arterial thrombosis limb at 0.7%. These listed terms do not replace the group-level counts or provide a complete account of every event.

Safety interpretation should account for the size of the groups, the observation period, and the registry's event definitions. The treatment schedule and primary assessment extend through week 6, and the record does not provide longer-term safety results in the registry record reported. Differences in counts alone should not be read as proof of a treatment-related effect.

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

The results describe a randomized comparison of budesonide foam with matching placebo in participants with active mild to moderate ulcerative proctitis or proctosigmoiditis. At week 6, the posted remission percentages were 38.3% for budesonide and 25.8% for placebo. The unadjusted risk difference was 0.126, with reported interval limits of 0.015 and 0.237. The sponsor's reported logistic regression test gave p = 0.032. Together, these statistics describe the observed primary comparison and its sampling uncertainty under the reported or recalculated analyses.

The result does not establish that every participant assigned to budesonide achieved remission, or that every participant assigned to placebo failed to do so. Nor does it show that all MMDAI components changed in the same way. The endpoint required a combined criterion, and the registry record does not report separate primary estimates for the components that formed it.

The findings do not establish effects beyond the week-6 assessment, in populations with different disease severity or location, or under different treatment schedules. They do not resolve how results vary across subgroups, because subgroup estimates are not reported in the registry record. The permitted continuation of established oral 5-aminosalicylic acid treatment also forms part of the study context; the record does not provide results stratified by its use.

The statistical result is not a guarantee of an individual outcome and should not be interpreted as medical advice. The safety counts are descriptive and do not establish causation. The analysis also depends on the stated intention-to-treat population and LOCF handling of missing data, while details of missingness and sensitivity analyses are not reported. Overall, the posted findings support a defined short-term comparison on the specified composite endpoint, with limits on precision, generalizability, and interpretation of secondary and safety outcomes.

18. Why This Trial Matters Statistically

This trial illustrates how the definition of an endpoint shapes the statistical question. Remission was not a single symptom score; it required specified clinical and endoscopic criteria to be met together. The result is therefore an estimate of the percentage meeting that joint rule, rather than an estimate of change in every MMDAI measure or of an average change in total score.

It also illustrates the distinction between absolute effects and hypothesis tests. The recalculated risk difference of 0.126 describes an unadjusted contrast on the proportion scale, while the sponsor's logistic regression p-value describes a model-based test. The recalculated p-value is different because the analysis is different. Keeping the effect estimate, its interval, and the p-value conceptually separate helps avoid treating a test result as a measure of effect size or precision.

The record makes visible a further issue common to clinical trials: missing-data handling is part of the analysis, not a neutral detail. The primary result used LOCF, but the amount and pattern of missing data and alternative analyses are not reported. Likewise, the presence of multiple secondary outcomes matters for interpretation, while the registry record does not report a multiplicity strategy. These details affect how confidently one can distinguish a primary finding from a broader set of exploratory comparisons.

Finally, planning numbers are not a retrospective verdict on trial quality. The sample-size illustrations use the observed effect and explicit assumptions, while the original design justification is not reported. Such planning calculations show how assumptions about a target effect influence participant requirements; they do not reveal why this study enrolled its observed number. Together, these features make the trial useful for understanding endpoint construction, analysis choices, uncertainty, and the limits of registry reporting.

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 primary endpoint was assessed at week 6, and the record does not report longer-term efficacy results. The study population was restricted to active mild to moderate ulcerative proctitis or proctosigmoiditis, so the posted findings do not directly describe other disease locations or severity groups. Participants could maintain established oral 5-aminosalicylic acid treatment up to 4.8 grams/day, but the registry record does not report results by background-treatment use.

The primary analysis used LOCF for missing data. The amount of missing data, reasons for missingness, and sensitivity analyses are not reported in the registry record. Because LOCF carries a previous observation forward, the result depends in part on an assumption about outcomes after the last observed assessment. The available information does not show how alternative missing-data assumptions would affect the estimate.

The sponsor's reported analysis is identified as logistic regression, but the registry record does not report model details, covariates, a model-based effect estimate, or its interval. The recalculated comparison is unadjusted, so it is not a substitute for missing model details. The record also does not report the original sample-size justification or a multiplicity plan for the 9 secondary outcomes. Those omissions constrain interpretation of the secondary findings and the design rationale.

Numerical results are available for three secondary outcomes in the record details, while results for the other listed secondary outcomes are not reported in the registry record. The safety counts are not accompanied by event-level timing, duration, or attribution details in the registry record reported. These limitations mean that the posted record supports a focused week-6 comparison but offers limited information about longer-term outcomes, robustness to analytic assumptions, and detailed safety interpretation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Budesonide Foam for Participants With Active Mild to Moderate Ulcerative Proctitis or Proctosigmoiditis — NCT01008410.
• Registry record last updated 2019-08-14; status last verified 2019-07.
• Results first posted 2019-08-14.
• 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

NCT01008410 is a completed phase 3, randomized, triple-masked, parallel-group comparison of rectal budesonide foam and matching placebo in participants with active mild to moderate ulcerative proctitis or proctosigmoiditis. The registry record lists 265 participants enrolled. Treatment followed a twice-daily schedule for 2 weeks and a once-daily schedule for 4 weeks.

The primary endpoint was week-6 remission, defined using endoscopy, rectal bleeding, and stool-frequency criteria. The reported percentages were 38.3% for budesonide and 25.8% for placebo. The sponsor's logistic regression analysis reported p = 0.032; an unadjusted recalculation gave a risk difference of 0.126 with interval limits of 0.015 and 0.237.

The primary population included all randomized participants, with missing data handled using LOCF. The registry record does not report the original sample-size rationale, multiplicity strategy, detailed regression specification, or sensitivity analyses for missing data. Safety counts and selected secondary results provide additional context, but their interpretation is limited by the reporting details available.