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 (NCT01008423), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Achieved Remission.

2. Clinical Question

The clinical question is about the result of a specified treatment schedule over 6 weeks in participants with active disease, not about every possible dose, duration, or form of treatment. Remission was defined using multiple MMDAI components, so the primary endpoint required meeting a combination of clinical and endoscopic criteria. It was not simply a change in one symptom or a total score.

The trial also reported secondary outcomes involving rectal bleeding, endoscopic findings, and combinations of MMDAI measures. These outcomes give additional views of disease activity, but the primary comparison is the remission endpoint defined in advance in the registry record. The registry record does not report detailed numerical results for every listed secondary outcome.

3. Trial Design

This was a phase 3, randomized, parallel-group study comparing rectal budesonide foam with matching placebo. The registry reports enrollment of 281 participants and lists the study as completed. The recorded start date is 2009-11-20, and the primary completion date is 2013-03-18. The sponsor was Bausch Health Americas, Inc.

The official title describes the study as double-blind, while the registry design fields describe masking as triple. The registry record does not identify which groups of people were masked, so the specific meaning of that masking designation cannot be established from the record alone. The study was randomized, but the method used to generate or conceal the allocation sequence is not reported in the registry record.

Participants assigned to budesonide received 2 mg/25 mL rectally twice daily for 2 weeks, followed by once-daily dosing for 4 weeks. Participants assigned to placebo received matching foam on the same schedule. The primary endpoint was assessed at Week 6. Previously established oral 5-ASA could be continued at doses up to 4.8 g/day.

The primary analysis population was ITT, including all randomized participants, with missing endpoint data imputed using last observation carried forward. The registry record does not report the original sample-size justification, the assumptions used in the trial's design, details of the randomization procedure, or whether interim analyses were planned or conducted. It also does not report a fuller statistical analysis plan describing covariate adjustment or the handling of multiple endpoints.

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 information from the Modified Mayo Disease Activity Index (MMDAI): an endoscopy score at most 1, a rectal bleeding score of 0, and improvement or no change from baseline in the stool-frequency subscale.

The MMDAI evaluates stool frequency, rectal bleeding, physician's global assessment, and endoscopy findings. Each index has a score from 0 to 3, and the total score can range up to 12. The primary definition draws on selected components rather than requiring a particular total score. It therefore captures a specific combination of symptoms and endoscopic status at the end of treatment.

A combined endpoint is used to represent more than one aspect of disease activity in a single outcome. It can make the trial question clinically interpretable as a proportion meeting a defined state, while also making the result dependent on every component of the definition. A participant who does not meet one required component is not counted as achieving this defined remission, even if another component has improved.

The registry specifies the ITT population and last observation carried forward for missing data. The amount and pattern of missing endpoint data, and how the imputation affected the remission counts, are not reported in the registry record. The endpoint describes status at Week 6; the registry entries do not establish persistence after treatment or provide a longer-term assessment of remission.

7. Results Posted in the Registry

• Budesonide: 44.0% (59/134) versus 22.4% (33/147) on control; risk difference 21.6 percentage points (95% CI 10.8 to 32.4), risk ratio 1.96 (1.37–2.80); unadjusted two-proportion z-test p = <0.001.

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: 50.0% (67/134) versus 28.6% (42/147) on control; risk difference 21.4 percentage points (95% CI 10.2 to 32.6), risk ratio 1.75 (1.29–2.38); unadjusted two-proportion z-test p = <0.001.
• 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: 56.0% (75/134) versus 36.7% (54/147) on control; risk difference 19.2 percentage points (95% CI 7.8 to 30.7), risk ratio 1.52 (1.17–1.98); unadjusted two-proportion z-test p = 0.001.
• 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 (BF) 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: 46.3% (62/134) versus 23.8% (35/147) on control; risk difference 22.5 percentage points (95% CI 11.6 to 33.4), risk ratio 1.94 (1.38–2.74); unadjusted two-proportion z-test p = <0.001.
• 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 secondary outcomes cover several related aspects of disease activity, including rectal bleeding, endoscopic findings, and combinations of MMDAI components. For the secondary outcomes with numerical comparisons posted, the proportions are directionally consistent with the primary remission result: more participants in the budesonide group met the specified outcome than in the placebo group. This broad alignment provides supporting context, but it is not a substitute for the primary endpoint.

Secondary endpoints can help describe which features of the overall clinical and endoscopic picture contributed to the pattern. They may also provide evidence that is more focused on a particular symptom or assessment component. Because they are related measures, however, their results are not independent confirmations of the primary finding. A pattern across related outcomes can be informative without multiplying the strength of evidence as if each were a separate trial.

The registry lists additional secondary outcomes, but detailed numerical results are not reported for every listed outcome in the registry record. The numerical secondary comparisons shown in the record are unadjusted recalculations, and the registry does not report sponsor analyses for those comparisons. Their p-values should therefore be interpreted cautiously.

When many outcomes are examined, the chance of at least one apparently notable result can rise even if no true effect exists for any outcome. Multiplicity procedures can control this risk, for example by adjusting the decision threshold or using a prespecified testing hierarchy. Whether such procedures were planned or applied is not reported in the registry record. Without that information, unadjusted secondary results carry less evidentiary weight than the designated primary endpoint.

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 (BF) 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

The primary outcome is binary at the participant level: each participant either met the remission definition at Week 6 or did not. A percentage is a direct way to describe the frequency of this event in each randomized group. It is readily interpretable, but the observed percentage alone does not convey how much statistical uncertainty surrounds the estimate or how the groups compare.

What does a risk ratio describe?

A risk ratio compares the event proportion in one group with the event proportion in another. A value of 1 represents equal proportions on this scale; a value above 1 represents a larger proportion in the first group, and a value below 1 represents a smaller proportion. The recalculated risk ratio for remission is 1.961. Its confidence interval, 1.374 to 2.8, lies above 1. This is a relative comparison: it does not directly express the absolute difference in percentage points.

A risk difference is another way to compare groups. It subtracts the event proportion in the control group from the event proportion in the intervention group. This scale describes the absolute separation between the observed proportions and is often easier to relate to an expected number of events in groups of a given size. The posted summaries also support a simple unadjusted risk-difference analysis, but the estimate and interval have more than three decimal places and are not reproduced.

Why distinguish the registry analysis from a recalculation?

The registry's reported analysis used logistic regression and reports p < 0.001. Logistic regression models the probability of a binary outcome on a transformed scale and can incorporate specified covariates, although the registry record does not report which covariates, if any, were included. The simple unadjusted recalculation instead uses the group counts and totals posted for the endpoint. It does not reproduce an adjusted model.

Different analysis methods can yield different numerical estimates, intervals, or p-values because they use different modeling assumptions or adjustments. A recalculation from summary counts is useful as a transparent check of the broad contrast, but it is not a substitute for the sponsor's analysis. In this case, the registry marks no discrepancy, and both analyses point in the same direction. The sponsor's own analysis remains the relevant reported trial analysis.

What do p-values and confidence intervals contribute?

A p-value describes how unusual the observed data, or data more extreme, would be under a specified null hypothesis and analysis model. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of an effect. The reported p-values indicate statistical evidence against equal outcomes under their respective analyses. They do not establish that the result will be reproduced in every setting.

A confidence interval describes the uncertainty around an estimated effect under the method used to construct it. A narrower interval indicates greater precision on that scale, while a wider interval leaves more possible values compatible with the data and method. The interval for the recalculated risk ratio stays above the equal-outcome value of 1, but the interval still spans a range of possible relative effects. The confidence level and exact interval method are not reported in the registry record.

Why does over-dispersion matter?

Over-dispersion is a general concern when a statistical model assumes less variability than the data contain. It can lead to standard errors that are too small and intervals or tests that appear more certain than warranted. The primary endpoint is binary and the registry identifies logistic regression, but the record does not report a dispersion assessment or model diagnostics. Over-dispersion is therefore a general modeling consideration, not a reported finding about this trial.

The sample-size planning figures use a normal approximation and equal allocation, as stated in the registry entries. Those assumptions make the figures planning illustrations rather than reconstructions of the trial's actual design. The original design assumptions, including its intended effect size and sample-size justification, are not reported in the registry record.

11. Confidence Intervals and Precision

The arm percentages give a direct description of observed remission: 44.0% for budesonide and 22.4% for placebo. A confidence interval adds information about uncertainty in a comparison, rather than treating the observed estimate as exact. For the simple recalculated risk ratio, the estimate is 1.961 and the interval runs from 1.374 to 2.8.

The interval is on the relative scale. Its lower and upper limits are both above the equal-outcome value of 1, so the interval does not include that null value. At the same time, the interval spans a range of relative effects; it is not a claim that the true effect must equal the point estimate. The confidence level and interval construction method are not reported in the registry record, which limits a fuller assessment of the interval's calibration.

Precision depends on the observed information and the analysis method. The groups included 134.0 and 147.0 participants, and the endpoint is a proportion, so the number of remission events also contributes to the uncertainty. The registry provides event counts of 59 and 33 for the budesonide and placebo groups in the comparison summary. The interval should be read as uncertainty around a group contrast, not as a range in which individual participant outcomes fall.

The displayed group percentages and an interval for a relative effect answer related but distinct questions. Percentages show the observed outcome frequency in each arm; the relative interval describes uncertainty in a ratio of those frequencies. Neither alone captures uncertainty related to missing-data assumptions or limits of generalizability. Missing-data sensitivity analyses and further interval details are not reported in the registry record.

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. They illustrate group sizes under the stated planning assumptions: a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row plans for a stated fraction of the observed effect, and the figures are based on the observed primary result rather than the trial's original design assumptions.

For planning for 100% of the observed effect, the figures are 74 participants per arm for 80% power and 99 participants per arm for 90% power. For planning for 75% of the observed effect, the figures are 126 participants per arm for 80% power and 169 participants per arm for 90% power. For planning for 50% of the observed effect, the figures are 270 participants per arm for 80% power and 361 participants per arm for 90% power.

In plain terms, the 80% power column gives the estimated group size for a design with an 80% chance of detecting the specified effect under the planning assumptions if that effect were present. The 90% power column describes the corresponding design target with a higher chance of detection. These are planning probabilities, not guarantees for a particular study. A smaller effect is harder to detect, so the planning figures rise as the target effect is reduced.

The registry record does not report the assumptions used for the trial's original sample-size calculation. These figures are a planning illustration derived from the observed effect, not observed power. A sample-size calculation cannot establish what the trial would have found under a different design or effect.

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 = 0.224; treatment proportion p₁ = 0.440; average p̄ = 0.332.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6662 = 1.3057.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6485 = 0.5458.
4. n = (1.3057 + 0.5458)² / (0.2158)² = 73.6, rounded up to 74 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 <- 0.224489795918367                          # control proportion
p1 <- 0.440298507462687                          # 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(1008423)
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 = 74 (80% power), 99 (90% power)
 75% of observed effect: n per arm = 126 (80% power), 169 (90% power)
 50% of observed effect: n per arm = 270 (80% power), 361 (90% power)
power.prop.test: 73.6 
Simulated power at n = 74 per arm: 0.808 (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 reports the sponsor's primary comparison as logistic regression with a superiority analysis and p < 0.001. It does not provide the regression effect estimate, its confidence interval, or details of the model specification. The sponsor's p-value is therefore the reported model-based result, but the registry record does not allow a full reconstruction of that analysis.

The simple recalculation from posted group summaries reports a risk ratio of 1.961, with a confidence interval from 1.374 to 2.8, and p < 0.001. This calculation is unadjusted and is not the same as the sponsor's logistic-regression analysis. The estimates and p-values should be understood in light of the methods that generated them, rather than treated as competing versions of one identical calculation.

The registry indicates no discrepancy between the posted summary and the reported analysis. Both analyses support the same direction of comparison, but the sponsor's analysis is the trial's reported analysis and takes precedence if a discrepancy arises. The absence of a discrepancy flag does not supply the missing model details or an adjusted effect estimate.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies remission at Week 6 as the primary endpoint and lists multiple secondary outcomes involving MMDAI subscales and combinations of measures. Testing several outcomes creates a multiplicity issue: the more comparisons made, the greater the opportunity for chance findings. A prespecified hierarchy or statistical adjustment can help control that risk, but the registry record does not report whether either approach was used. The unadjusted secondary comparisons should not be treated as though multiplicity had been accounted for.

The primary endpoint analysis used the ITT population, defined in the registry as all randomized participants. This approach retains participants according to randomization and supports a comparison based on assigned groups. Missing data were imputed using last observation carried forward (LOCF), which carries a participant's last recorded observation forward to the endpoint when a later value is missing.

LOCF makes an analysis possible when endpoint values are missing, but it relies on an assumption that the last observed value is a suitable stand-in for the missing endpoint. That assumption may not fit every participant's subsequent course. The registry record does not report the number of missing primary outcomes, the reasons for missingness, whether missingness differed by group, or sensitivity analyses using alternative imputation methods. The effect of LOCF on the result therefore cannot be evaluated from the reported details.

The registry record also does not provide a detailed statistical analysis plan, the full logistic-regression specification, or information about interim analyses. It is not possible to determine from the registry record whether any covariate adjustments, multiplicity procedures, or additional population analyses were prespecified. These absences do not change the reported arm percentages, but they constrain assessment of analytic choices and robustness.

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: abdominal pain (0.7%), colitis ulcerative (0.7%), acute generalised exanthematous pustulosis (0.7%).

The registry reports serious adverse events affecting 3 participants in the budesonide group and 0 in the placebo group. The groups at risk were 134 and 147, respectively. The serious-event terms listed were abdominal pain, colitis ulcerative, and acute generalised exanthematous pustulosis, each reported as 0.7%.

Other adverse events were reported for 57 participants in the budesonide group and 54 in the placebo group. The registry reports 0 deaths in each group. These counts describe events recorded in the trial; they do not by themselves establish that an event was caused by a treatment or allow comparison of event severity, duration, or clinical course.

Serious adverse event counts are not a complete safety profile. Their interpretation depends on how events were defined, collected, and attributed, and on the duration of observation. Detailed event descriptions and a fuller account of safety monitoring are not reported in the registry record. The counts should be read as descriptive trial data rather than as a stand-alone estimate of risk in other populations or settings.

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

The posted result describes the proportion meeting a defined remission criterion after 6 weeks of the study treatment schedule. The observed proportions were 44.0% with budesonide and 22.4% with placebo. The recalculated relative comparison and the reported logistic-regression p-value both indicate a difference in the direction of a higher remission proportion in the budesonide group in this trial.

This result does not establish that every participant experienced improvement, or that a participant who did not meet the remission definition had no improvement at all. The endpoint was a combined threshold based on endoscopy, rectal bleeding, and stool frequency. It classified remission according to that definition at the Week 6 assessment; it was not a complete account of every aspect of a participant's health.

The finding is specific to participants with active mild to moderate ulcerative proctitis or proctosigmoiditis enrolled in this study, the rectal foam schedules used, the allowed background 5-ASA treatment, and the registry's missing-data approach. The registry does not report longer-term remission, durability after treatment, or outcomes for different doses and schedules. Applicability to people outside the studied population cannot be established from these results alone.

A statistically detectable group difference does not, by itself, determine whether the difference is important to participants or how it should affect an individual treatment decision. No medical advice follows from the statistical comparison alone. The result should be interpreted alongside the endpoint definition, uncertainty, study design, safety information, missing-data limitations, and other relevant evidence, which is not fully described in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical endpoint needs a precise definition. “Remission” can mean different things across studies; here, the registry defines it through a combined set of endoscopic and clinical criteria. That definition determines which participants count as events and therefore shapes the percentages, comparison, and interpretation.

It also demonstrates the value of distinguishing absolute and relative comparisons. The group percentages describe how often remission was recorded in each arm, while the risk ratio expresses the relationship between those proportions. Neither scale is sufficient for every question. Reporting the scale clearly helps readers understand what an estimate says and what it leaves out.

The record also makes visible the difference between a sponsor's model-based analysis and a simple recalculation from group summaries. The two methods may rely on different assumptions and answer slightly different analytic questions. Agreement in direction is reassuring as a consistency check, but a recalculation cannot replace missing details of the reported model or a full analysis plan.

Finally, this example highlights limits of registry reporting. A primary outcome and analysis population are specified, but information on multiplicity, missing-data sensitivity analyses, original sample-size planning, and model details is not reported. Those omissions matter because statistical interpretation depends not only on the observed percentages, but also on how outcomes were selected, missing observations handled, and uncertainty modeled.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves important details unavailable for evaluating the primary analysis. Although it reports logistic regression and a p-value, it does not give the model specification, adjusted effect estimate, or confidence interval for that analysis. The simple recalculation can show the contrast in the posted group summaries, but it cannot reproduce or verify an adjusted model.

The ITT analysis used LOCF for missing data, but the record does not report the number of missing primary outcomes, reasons for missingness, or sensitivity analyses under other assumptions. Because remission is a combined endpoint, interpretation also depends on the recorded values for its component measures; component-level missingness and its handling are not described.

The registry lists multiple secondary outcomes, but it does not report whether multiplicity was controlled or whether a hierarchy was prespecified. Detailed numerical results are not available in the record for every listed secondary outcome. This limits the strength of conclusions drawn from secondary comparisons and prevents a complete account of the consistency of all planned outcomes.

The primary result is assessed at Week 6. Longer-term outcomes, persistence of remission, and the results of alternative schedules are not reported in the registry record. The registry also does not report the original sample-size justification, details of randomization or allocation concealment, or which groups of people were masked, despite the differing masking descriptions in the title and design fields. These limitations constrain appraisal of robustness and generalizability; they do not negate the observed Week 6 comparison.

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 — NCT01008423.
• 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

NCT01008423 is a completed phase 3 randomized parallel-group study of rectal budesonide foam versus matching placebo in participants with active mild to moderate ulcerative proctitis or proctosigmoiditis. Enrollment was 281. Budesonide was given twice daily for 2 weeks and once daily for 4 weeks; placebo followed the same schedule. Established oral 5-ASA treatment could continue at doses up to 4.8 g/day.

The primary endpoint was remission at Week 6, defined using endoscopy, rectal bleeding, and stool frequency measures from the MMDAI. The registry reports remission in 44.0% of the budesonide group and 22.4% of the placebo group. Its logistic-regression analysis reports p < 0.001; an unadjusted recalculation reports a risk ratio of 1.961, with a confidence interval from 1.374 to 2.8.

The primary analysis included all randomized participants and used LOCF for missing data. The registry does not report the original sample-size assumptions, detailed model specification, multiplicity approach, or missing-data sensitivity analyses.