Efficacy of Alicaforsen in Pouchitis Patients Who Have Failed to Respond to at Least One Course of Antibiotics: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of Alicaforsen in Pouchitis Patients Who Have Failed to Respond to at Least One Course of Antibiotics (NCT02525523), a randomized phase 3 study. The primary outcome is Proportion of Patients With Endoscopic Remission.

2. Clinical Question

The clinical question concerns an endoscopic outcome in a population described as having ongoing pouchitis despite antibiotic treatment. It is narrower than a question about symptoms alone: the primary endpoint is based on the endoscopic score, while the trial also planned symptom diaries, histopathology, quality-of-life assessments, and biomarker collection. Those additional assessments do not change the definition of the posted primary outcome.

The posted counts indicate that the outcome was uncommon in both reported groups. They do not by themselves establish that the groups had identical underlying outcome rates. The estimated between-group difference and its uncertainty are relevant to judging how much the observed data distinguish possible effects. The registry record does not report a treatment effect on the other assessments in the brief summary, and no secondary results are posted.

3. Trial Design

This was a randomized, parallel-group, placebo-controlled Phase III trial sponsored by Atlantic Pharmaceuticals Ltd. The registry reports enrollment of 138 and status as completed. Participants were allocated to alicaforsen or matching placebo, with a 1:1 randomization plan stated in the brief summary. The record classifies masking as triple and the model as parallel.

The brief summary describes a screening period of <2 weeks before baseline eligibility assessment. At the baseline visit, participants were assigned to one of the two treatment groups. Alicaforsen was administered as a 240 mg enema once nightly for 6 weeks; placebo was administered once daily for the same duration. Participants were scheduled for safety and efficacy assessments at Week 3, Week 6, Week 10, Week 18, and Week 26 after baseline.

Endoscopic examinations were planned during screening and at Week 6 and Week 10. Where technically feasible, an endoscopy was to include at least one biopsy for histopathology. Symptoms associated with pouchitis were to be recorded daily in a patient diary. The brief summary also mentions quality of life, routine blood testing, and blood and stool collection for relevant biomarkers. It describes restrictions on introducing or changing pouchitis medications, except as allowed by the protocol.

The primary outcome reported in the results concerns endoscopic remission at Week 10. The outcome counts were three among 65 participants in the alicaforsen group and three among 61 participants in the placebo group. The record does not report the reasons that the outcome denominators differ from the enrollment figure or give further details about participant flow, exclusions, or missing Week 10 assessments. The registry’s original sample-size justification 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

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.

6. Primary Endpoint

The registry lists the primary outcome as Proportion of Patients With Endoscopic Remission, measured over Week 10.

The primary endpoint was the proportion of participants with endoscopic remission at Week 10. The registry describes remission as absence of friability and ulceration, represented by a modified MAYO score of ≤1. It also describes the assessed group as patients with an improvement in endoscopic score between screening and Week 10, based on a reduced modified MAYO score.

Endoscopy provides a structured assessment of the pouch’s appearance. Using an explicit score threshold makes the endpoint operational: remission is classified according to specified endoscopic findings rather than an unstructured impression. This can make an outcome easier to compare across randomized groups, provided the assessment and scoring are applied consistently. The registry record does not report details of assessor training, central review, or procedures for resolving differences in scoring.

As a binary endpoint, each participant is classified as either meeting or not meeting the remission definition. The posted group results therefore give counts of participants meeting the endpoint, rather than changes in an average score. The result is specific to endoscopic remission at Week 10. It does not directly describe symptom relief, histopathologic findings, quality of life, or later outcomes. Although the trial brief summary mentions these other assessments, no secondary results are posted in the registry record.

The primary endpoint is useful for addressing the trial’s stated endoscopic question, but its interpretation depends on the outcome definition and the availability of assessments at the specified time. The registry record does not report how missing endoscopy data were handled or which analysis population was used for this endpoint.

7. Results Posted in the Registry

• Alicaforsen: 4.6% (3/65) versus 4.9% (3/61) on control; risk difference -0.3 percentage points (95% CI -7.8 to 7.1), risk ratio 0.94 (0.20–4.47); unadjusted two-proportion z-test p = 0.936.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: a participant either met the Week 10 remission definition or did not. For a binary endpoint, the basic descriptive results are the number meeting the definition and the number assessed in each group. The posted counts were three of 65 for alicaforsen and three of 61 for placebo. This format preserves the actual observed event counts and makes clear that the result was based on few endpoint events.

What does the risk difference describe?

In general, a risk difference subtracts the outcome rate in one group from the outcome rate in the other. It is an absolute measure: its scale reflects the difference in the probability of the event, rather than a ratio of probabilities. The posted estimate is -0.003 for alicaforsen relative to placebo. A negative value indicates that the observed remission rate was lower in the alicaforsen group under that comparison direction. The two groups had the same event count, while their denominators differed, so the estimated difference is not exactly zero.

The estimate is a summary of the observed data, not a guarantee about the underlying effect. In general, random variation can make an estimated difference depart from the true effect, especially when the outcome is uncommon. The confidence interval communicates that uncertainty. Because the reported interval includes zero and extends to values on either side, the result is compatible with an effect favoring either group as well as with no difference.

How should the p-value be read?

In general, a p-value assesses how compatible the observed data are with a specified null model, using a chosen statistical test. It does not measure the size or clinical importance of an effect, and it is not the probability that the null model is true. The posted unadjusted p-value is 0.936. That value does not provide evidence of a clear separation in the observed endpoint results, but it also cannot establish equivalence. A formal equivalence or non-inferiority conclusion would require appropriate prespecified margins and methods; these are not reported in the registry record.

The comparison is labelled unadjusted. In general, an unadjusted comparison estimates the group contrast without accounting for other variables in a regression or covariate-adjusted model. Adjustment can be useful when specified in advance and appropriate for the design and data. The registry record does not report an adjusted result, covariates, or further details of the test used for the posted p-value.

Why does the small event count matter?

In general, the precision of a binary-outcome estimate depends on the number of participants and on how many outcomes occur. When few events are observed, a small change in the event count can noticeably affect the estimated rate and the difference between groups. This contributes to a wide range of effect values that remain compatible with the data. Here, the observed endpoint count was three in each group, so the estimate should be read with its uncertainty rather than as a definitive comparison.

The posted effect measures also include relative measures, but their detailed estimates are not needed to understand the primary result. Relative measures compare outcome rates as a ratio, whereas the risk difference expresses an absolute contrast. In general, relative measures can appear large or small depending on the baseline event rate, and may be unstable when event counts are sparse. Whichever scale is used, the small number of observed remission outcomes limits precision.

What analysis details are unavailable?

The registry record does not report the original statistical analysis plan, the exact analysis population, the handling of missing Week 10 assessments, or whether any participants were excluded from the primary comparison. It also does not report whether endpoint assessments were centrally reviewed or whether any covariates were planned for adjustment. These details matter because the analyzed population and the handling of incomplete outcome data can affect an estimate, particularly when event counts are limited.

In general, randomized allocation supports a fair comparison by reducing systematic differences between groups at assignment, while masking can reduce some forms of assessment or behavior-related bias. The record describes randomized allocation and triple masking. Those design features do not remove the need to understand follow-up, outcome ascertainment, and analysis choices. Since these details are not reported, the posted unadjusted comparison is best interpreted as the estimate available from the registry record rather than as a full reconstruction of the trial’s analysis.

The sample-size figures are planning illustrations derived from the observed effect, not evidence about the study’s original design or its achieved ability to detect an effect. The original sample-size assumptions are not reported in the registry record. The planning assumptions and their implications are described separately in plain language.

10. Confidence Intervals and Precision

The point estimate for the risk difference is -0.003. The reported confidence interval extends from a negative value to a positive value, so it includes zero. In general, a confidence interval is a range of values that reflects sampling uncertainty under the method used to calculate it. It is not a guarantee that the true effect lies within that particular interval, and it should not be read as a probability statement about the treatment effect.

The interval’s inclusion of zero means the data do not rule out no difference. Its extension in both directions also means that the posted result is compatible with effects favoring either group. This is a key distinction between the observed estimate and the precision of that estimate: the estimate is close to zero, but uncertainty around it remains substantial. The same observed count in each group does not make the comparison precise, particularly when the number of remission outcomes is small.

The reported p-value is 0.936, but a p-value and a confidence interval answer related, not identical, questions. The p-value summarizes compatibility with a null model under the test used; the interval conveys the range of effect values compatible with the data under the interval procedure. Neither establishes that the groups are equivalent. The registry record does not report an equivalence margin or a precision target for the primary endpoint.

Precision should also be considered in light of the analysis details that are not reported. The record does not state how missing Week 10 assessments were handled or which analysis population was used. These omissions limit a full assessment of uncertainty and potential sensitivity to analysis choices. The posted interval is therefore useful for describing the reported comparison, but the registry record does not contain all the information needed to evaluate every source of uncertainty.

11. 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 participants or total events. They are illustrations based on the observed effect and are not the trial’s original sample-size justification; that justification is not reported in the registry record. The assumptions listed for these illustrations 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 planning based on 100% of the observed effect, the illustration gives 77,797 participants per arm for 80% power and 104,148 participants per arm for 90% power. For planning at 75% of the observed effect, the corresponding figures are 139,349 and 186,549 participants per arm. For planning at 50% of the observed effect, they are 315,880 and 422,873 participants per arm. These are planning illustrations, not recommendations or a claim about what the trial needed when it was designed.

In general, power is the probability that a study will detect an effect of a specified size under the assumed model and conditions. The 80% column describes the planned sample size for an analysis with an 80% chance of detecting the specified effect if that effect is present and the assumptions hold. The 90% column describes the corresponding sample size for a higher chance of detection. Smaller effects require more participants to distinguish them from random variation, which is why the planning figures increase as the assumed fraction of the observed effect decreases.

These numbers are not observed power. They are hypothetical sample-size calculations using the observed effect as a planning reference, and the observed effect is itself uncertain. The registry record does not report whether its original design used these assumptions or any similar assumptions.

12. 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 = 0.049; treatment proportion p₁ = 0.046; average p̄ = 0.048.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3013 = 0.5906.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3013 = 0.2536.
4. n = (0.5906 + 0.2536)² / (-0.0030)² = 77,796.9, rounded up to 77,797 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 <- 0.0491803278688525                          # control proportion
p1 <- 0.0461538461538462                          # 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(2525523)
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 = 77,797 (80% power), 104,148 (90% power)
 75% of observed effect: n per arm = 139,349 (80% power), 186,549 (90% power)
 50% of observed effect: n per arm = 315,880 (80% power), 422,873 (90% power)
power.prop.test: 77796.9 
Simulated power at n = 77,797 per arm: 0.801 (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.

13. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns the chance of false-positive findings when several outcomes, comparisons, time points, or analyses are examined. In general, testing many questions can raise that chance unless the analysis plan accounts for it. The registry record identifies a primary endpoint, which helps distinguish the main question from other assessments. The brief summary also describes symptoms, histopathology, quality of life, and biomarkers, but no secondary outcome results are posted.

The registry record lists no posted analyses beyond the primary comparison. It does not report a multiplicity adjustment, a hierarchy of secondary outcomes, or a plan for handling multiple time points. Because secondary results are not posted, the possible effects on those outcomes cannot be assessed from this record. The original statistical analysis plan is not reported in the registry record, so it is not possible to determine from this information whether multiplicity procedures were planned or used.

Missing data are another important consideration. The primary outcome denominators are 65 for alicaforsen and 61 for placebo, while overall enrollment is reported as 138. The registry record does not explain the difference between these figures, provide a participant-flow account, or report whether every randomized participant had an evaluable Week 10 endoscopy. It also does not state how missing primary outcomes were handled, whether any imputation was used, or whether sensitivity analyses were performed.

The analysis population is not reported in the registry record. In general, an analysis of all randomized participants and an analysis limited to participants with observed outcomes can answer somewhat different questions, especially if outcome availability is related to prognosis or treatment assignment. The record does not say whether the primary comparison followed an intention-to-treat approach, a per-protocol approach, or another definition. No assumption about the analysis population or missing-data method should therefore be inferred from the posted counts alone.

These reporting gaps do not change the arithmetic of the posted comparison, but they limit how fully its robustness can be assessed. A complete interpretation would benefit from the prespecified analysis plan, participant disposition, endpoint availability, and details of any multiplicity or missing-data procedures. Those details are not reported in the registry record.

14. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: diarrhoea (1.4%), gastrointestinal obstruction (1.4%), small intestinal obstruction (1.4%), anal absess (1.4%), lipoma (1.4%).

The registry reports serious adverse events affecting four participants in the alicaforsen group and two participants in the placebo group. Each group’s serious-event figures use 69 participants at risk. For other adverse events, the record reports 19 affected participants in the alicaforsen group and 20 in the placebo group, again with 69 at risk in each group. Deaths are reported as zero in both groups.

These are group-level counts, not evidence that every event was caused by the assigned treatment. The registry record does not provide event-level narratives or a full account of how seriousness, relatedness, duration, or recurrence was assessed. The listed serious-event terms include Diarrhoea, Gastrointestinal obstruction, Small intestinal obstruction, Anal Absess, Lipoma, and Facial Paralysis, each reported as 1.4%. The record does not clarify the group attribution for those listed terms in the information.

In general, adverse-event counts describe events recorded during a study, while causal attribution requires additional clinical and methodological assessment. They should be read alongside exposure, follow-up, and the trial’s event definitions. The figures do not establish comparative safety by themselves, and they do not replace a complete safety report. The registry record does not report further detail on event timing, severity beyond serious-event classification, or the statistical comparison of safety outcomes.

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

The posted result describes endoscopic remission at Week 10 in the randomized alicaforsen and placebo groups. Three participants met the endpoint in each group. The estimated risk difference was -0.003, and the reported unadjusted p-value was 0.936. The confidence interval includes zero and extends in both directions, indicating that the result does not precisely determine the direction or size of the underlying difference.

This finding does not establish that alicaforsen and placebo are equivalent. Demonstrating equivalence would require a prespecified equivalence margin and an analysis designed to assess whether the effect falls within that margin; those details are not reported in the registry record. Nor does the result prove that there is no effect. The limited number of observed remission outcomes leaves uncertainty about effects that the trial’s posted estimate cannot distinguish clearly.

The result is specific to the registry’s primary endpoint definition and Week 10 assessment. It does not answer whether there were differences in symptom diaries, histopathology, quality of life, biomarkers, or outcomes at other visits. Although the brief summary describes those assessments and later follow-up, secondary outcome results are not posted in the registry record. No conclusion about those outcomes follows from the primary endpoint comparison.

The trial design features—random allocation, placebo control, and masking—are relevant strengths for comparing groups, but they do not resolve the reporting gaps about analysis populations, missing endoscopy data, or the original statistical plan. The posted data can be described accurately without claiming more than they show: the observed endpoint counts were the same, the estimated difference was close to zero, and uncertainty remains substantial.

These statistics are not medical advice and do not determine an individual treatment choice. They are an account of the posted trial results and their precision, rather than a general claim about treatment efficacy or safety.

16. Why This Trial Matters Statistically

This trial is statistically informative because it makes the difference between an observed result and a precise estimate visible. The same number of participants met the Week 10 remission definition in each group, and the estimated risk difference was close to zero. Yet the low number of observed outcomes means that the data do not tightly pin down the underlying group difference. Statistical interpretation therefore requires both the point estimate and the uncertainty around it.

The example also illustrates why a non-significant comparison is not evidence of equivalence. The reported p-value is 0.936, and the confidence interval includes zero, but neither result demonstrates that the treatments have identical effects. To support equivalence, the study would need an appropriate prespecified framework and margin, which are not reported in the registry record. Without that information, the appropriate conclusion is that the posted comparison does not clearly separate the groups, while meaningful uncertainty remains.

A second statistical issue is how endpoint choice shapes the question. The primary endpoint is an endoscopic remission measure at Week 10. The trial brief summary describes additional symptom, histopathology, quality-of-life, and biomarker assessments, but no secondary results are posted. Keeping the conclusion tied to the reported primary endpoint avoids treating an endoscopic result as if it summarized every aspect of the trial.

Finally, this record shows why transparent reporting of analysis populations, missing data, multiplicity, and design assumptions matters. The available outcome counts support a straightforward unadjusted comparison, but important details needed to evaluate its full robustness are not reported. The planning illustrations also demonstrate how strongly sample-size requirements can depend on the effect size a study aims to detect. These are general statistical lessons, not additional findings about the trial.

17. 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 interpretive questions unresolved. Although enrollment is reported as 138, the primary outcome denominators are 65 for alicaforsen and 61 for placebo. The record does not provide a participant-flow description or explain why these denominators differ from overall enrollment. It also does not state how many participants lacked a Week 10 endoscopic assessment or how such missing outcomes were treated.

The record does not report the primary analysis population, the detailed statistical analysis plan, or whether the primary comparison was adjusted for any baseline variables. It does not describe how endoscopic scores were assessed, whether assessors were centrally reviewed, or how score disagreements were managed. Those details could help readers assess the reliability of outcome classification and the sensitivity of the result to analysis choices.

The registry describes several planned assessments beyond the primary endpoint, including symptoms, histopathology, quality of life, and biomarkers, but no secondary outcome results are posted. Consequently, the available result gives a limited view of the trial’s planned evaluation. The record also does not report an original sample-size justification or its assumptions, so the planning illustrations based on the observed effect should not be mistaken for the trial’s design rationale.

The posted comparison is unadjusted, and its confidence interval indicates substantial uncertainty. The observed remission counts were small, and the record does not provide further analyses that might clarify the stability of the result. These limitations do not invalidate the reported counts; they define the boundaries of what can be concluded from the registry record.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Efficacy of Alicaforsen in Pouchitis Patients Who Have Failed to Respond to at Least One Course of Antibiotics — NCT02525523.
• Registry record last updated 2020-02-25; status last verified 2020-02.
• Results first posted 2020-02-25.
• 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.

21. Record Summary

The registry record describes a completed, randomized, double-blind, placebo-controlled Phase III trial of topical alicaforsen enema in people with active, chronic, antibiotic-refractory primary idiopathic pouchitis. The study compared alicaforsen, 240 mg once daily for 6 weeks, with matching placebo enema. Enrollment was 138.

The primary endpoint was endoscopic remission at Week 10. The posted counts were three participants among 65 in the alicaforsen group and three among 61 in the placebo group. The estimated risk difference was -0.003, with an unadjusted p-value of 0.936 and a confidence interval that includes zero. The result does not establish equivalence; uncertainty remains about the underlying difference.

The registry record does not report secondary outcome results, the primary analysis population, handling of missing Week 10 assessments, or the original statistical analysis plan and sample-size justification. Serious adverse events were reported for four participants in the alicaforsen group and two in the placebo group; deaths were reported as zero in both groups.