A Study to Evaluate the Efficacy and Safety of CC-93538 in Adult and Adolescent Participants With Eosinophilic Esophagitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy and Safety of CC-93538 in Adult and Adolescent Participants With Eosinophilic Esophagitis (NCT04753697), a randomized phase 3 study. The primary outcome is Change From Baseline in Mean Dysphagia Days (DD) at Week 24.

2. Clinical Question

The registry also lists histology outcomes at Weeks 24 and 48, including the proportion of participants below specified peak esophageal eosinophil-count thresholds. These secondary outcomes address tissue findings, while the primary outcome measures reported swallowing symptoms. The trial therefore addresses related but distinct aspects of eosinophilic esophagitis. Its posted results describe group-level changes and comparisons; they do not by themselves establish how an individual participant’s symptoms or histology would change.

3. Trial Design

This was a Phase 3, multicenter, multinational, randomized, double-blind, placebo-controlled parallel-group study. The registry lists the trial status as completed and enrollment as 430. The recorded start date is 2021-02-22, and the primary completion date is 2024-01-11. Celgene is listed as the sponsor.

The study had a 24-week Induction Phase followed by a 24-week Maintenance Phase. Participants were randomized among three treatment strategies: placebo through both phases; CC-93538 360 mg subcutaneously once weekly during induction followed by 360 mg once every other week during maintenance; or CC-93538 360 mg once weekly during both phases. In the every-other-week maintenance group, matching placebo was given on alternate weeks to maintain masking. The registry describes the masking as quadruple.

The primary endpoint was assessed at Week 24 and compares the weekly CC-93538 induction group with the placebo group. The posted primary outcome values are based on participants with observed values at the specified timepoint, within the registry’s stated Intent-to-Treat population definition. The reported sponsor analysis used ANCOVA and a difference in least squares means. Further detail on covariates, model specification, or handling of missing observations is not reported in the registry record.

The maintenance outcomes use Week 48 data and compare each active maintenance regimen with placebo. Those comparisons therefore address outcomes after the induction and maintenance sequence, not simply the Week 24 induction contrast. The registry lists 33 outcome measures and 22 analyses; it does not report the full statistical plan or explain how the analyses were selected or prioritized. The original sample-size justification and trial-specific design assumptions 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.

Pre-Treatment Period

Induction Phase

Reasons for not completing this period:

Maintenance Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Intent-to-Treat (ITT) population consist of all randomized participants and analyzed according to their randomized treatment group regardless of whether or not the participant received IP CC-93538 or placebo. Number of participants with observed values at the specified timepoint are included in the analysis.

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 Change From Baseline in Mean Dysphagia Days (DD) at Week 24, measured over Baseline (Day 1) and Week 24.

The primary endpoint is change from baseline in mean dysphagia days at Week 24. Dysphagia days were assessed using a modified daily symptom diary over the prior 14-day period. The diary included questions about solid food consumption, trouble swallowing, food moving slowly, food getting stuck in the throat or chest, actions taken for relief, and pain associated with swallowing. The endpoint definition uses diary responses about trouble swallowing, food moving slowly, or food getting stuck.

For each assessed period, the count was normalized using the number of measurable diary days: days when Questions 2 to 4 had been answered. The resulting mean dysphagia-days measure ranges from 0 to 14 for a 14-day period. A decrease from baseline represents fewer days meeting the endpoint’s symptom definition over the reporting period. The registry reports the outcome as a mean with standard deviation and identifies baseline as Day 1 and the assessment timepoint as Week 24.

This endpoint is used to quantify symptoms in a structured, repeated diary measure rather than relying only on a single retrospective report. It captures symptom frequency over a defined period, but it does not directly measure tissue inflammation. The registry does not report a threshold for a clinically meaningful change, so the statistical results alone cannot establish whether a particular difference is meaningful to participants. The endpoint also depends on diary completion: the record defines measurable days, but further rules for incomplete diaries are not reported.

7. Results Posted in the Registry

• Induction Phase - CC-93538 360 mg QW: mean -6.85 versus -4.98 on control; difference -1.87 (95% CI -2.99 to -0.75), standardized effect d = -0.36; 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 With Peak Esophageal Eosinophil Count <= 6/High-power Field (Hpf) at Week 48

• 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:
  • Maintenance Phase - CC-93538 360 mg QW: 37.5% (39/104) versus 4.9% (4/82) on control; risk difference 32.6 percentage points (95% CI 22.2 to 43.0), risk ratio 7.69 (2.86–20.64); unadjusted two-proportion z-test p = <0.001.
  • Maintenance Phase - CC-93538 360 mg Q2W: 34.3% (37/108) versus 4.9% (4/82) on control; risk difference 29.4 percentage points (95% CI 19.3 to 39.5), risk ratio 7.02 (2.61–18.92); 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 Maintenance Phase - CC-93538 360 mg QW than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Maintenance Phase - CC-93538 360 mg Q2W than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Peak Esophageal Eosinophil Count < 15/High-power Field (Hpf) at Week 24

• 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:
  • Induction Phase - CC-93538 360 mg QW: 53.0% (132/249) versus 4.7% (6/129) on control; risk difference 48.4 percentage points (95% CI 41.2 to 55.5), risk ratio 11.40 (5.17–25.11); 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 Induction Phase - CC-93538 360 mg QW than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Peak Esophageal Eosinophil Count < 15/High-power Field (Hpf) at Week 48

• 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:
  • Maintenance Phase - CC-93538 360 mg QW: 50.0% (52/104) versus 8.5% (7/82) on control; risk difference 41.5 percentage points (95% CI 30.1 to 52.8), risk ratio 5.86 (2.81–12.20); unadjusted two-proportion z-test p = <0.001.
  • Maintenance Phase - CC-93538 360 mg Q2W: 50.0% (54/108) versus 8.5% (7/82) on control; risk difference 41.5 percentage points (95% CI 30.3 to 52.7), risk ratio 5.86 (2.81–12.19); 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 Maintenance Phase - CC-93538 360 mg QW than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Maintenance Phase - CC-93538 360 mg Q2W than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the posted secondary outcomes, active-treatment groups had higher proportions meeting the specified eosinophil-count thresholds than placebo at the reported assessment times. The registry also reports sponsor analyses favoring the active groups for these comparisons. Considered alongside the primary symptom outcome, this pattern spans both a diary-based measure of dysphagia and tissue-based histology measures. The endpoints nevertheless represent different clinical domains and should not be combined into one effect estimate.

The Week 24 histology outcome is aligned with the induction-period comparison, while the Week 48 outcomes follow the maintenance regimens. Week 48 maintenance comparisons do not isolate the effect of maintenance dosing from the preceding induction sequence. The two active maintenance schedules are both compared with placebo; the posted analyses do not establish a direct statistical comparison between the two active schedules.

Secondary outcomes are generally less conclusive than a single prespecified primary outcome when many outcomes and comparisons are examined. Each additional test creates another opportunity for a result to appear statistically notable by chance. The registry lists 33 outcome measures and 22 analyses, but a multiplicity adjustment or a hierarchy controlling the family-wise error rate is not reported in the registry record. Therefore, the secondary p-values should be interpreted with caution, even when they are small.

The secondary results can add context and show whether findings extend beyond the primary measure, but they do not independently settle the primary question or demonstrate that every histology definition is equally informative. The thresholds, timepoints, populations with observed data, and analysis methods differ. A reader should focus on the overall pattern while retaining the uncertainty and multiplicity limitations rather than treating every result as a separate definitive conclusion.

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

• Percentage of Participants With Peak Esophageal Eosinophil Count <= 6/High-power Field (Hpf) at Week 48
• Percentage of Participants With Peak Esophageal Eosinophil Count < 15/High-power Field (Hpf) at Week 24
• Percentage of Participants With Peak Esophageal Eosinophil Count < 15/High-power Field (Hpf) at Week 48
• Change From Baseline in Mean Dysphagia Days (DD) at Week 48
• Change From Baseline in Eosinophilic Esophagitis (EoE) Endoscopic Reference Score (EREFS) at Week 24
• Change From Baseline in Eosinophilic Esophagitis (EoE) Endoscopic Reference Score (EREFS) at Week 48
• Change From Baseline in Mean Adjusted Eosinophilic Esophagitis Histology Scoring System (EoEHSS) Grade Score at Week 24
• Change From Baseline in Mean Adjusted Eosinophilic Esophagitis Histology Scoring System (EoEHSS) Grade Score at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a mean change in a count-like symptom measure. The registry reports group means and standard deviations, and the sponsor’s analysis is an ANCOVA comparing least squares means. The posted results also permit a simple unadjusted comparison calculated from the group summary statistics. These approaches answer related questions but are not identical: the re-calculation is an unadjusted summary-statistic comparison, whereas ANCOVA estimates a contrast from a model.

What does ANCOVA contribute?

As a general statistical method, analysis of covariance compares outcome means while accounting for selected covariates. An adjusted estimate can differ from a raw difference in group means because it conditions on the variables included in the model. The registry identifies ANCOVA and reports the least squares mean difference, but the covariates and detailed model specification are not reported in the registry record. The sponsor’s estimate should therefore be understood as the registry-reported model-based result, not reconstructed from the posted arm means alone.

How should the unadjusted re-calculation be read?

The re-calculated primary contrast is -1.87 days. It is a simple comparison based on the posted mean changes and is useful for a transparent summary-statistic view of the result. It does not reproduce the sponsor’s adjustment, account for unreported model details, or replace the reported ANCOVA. The registry’s discrepancy indicator is false, so there is no flagged disagreement requiring the sponsor’s own analysis to take precedence over the re-calculation. Even so, the sponsor’s analysis remains the reported trial analysis and should be distinguished from the simple re-calculation.

The standardized effect size is a way of expressing a mean difference relative to variability, rather than in the original days scale. It can help describe scale-free magnitude, but it is not itself a clinical-importance threshold. No such threshold is reported in the registry record. The standard deviation describes variation among observed participant outcomes; it does not describe uncertainty in the estimated group mean. That uncertainty is represented more directly by a standard error or confidence interval.

How are the binary outcomes analyzed?

The secondary eosinophil-count endpoints are binary response outcomes at specified thresholds: a participant either meets the threshold or does not. The posted percentages describe the fraction meeting each definition in each group. An unadjusted risk difference expresses the difference between those response proportions on the percentage-point scale. The re-calculated risk differences are based on the posted counts and group denominators; they are distinct from the sponsor’s reported analyses.

For the binary endpoints, the sponsor reports Cochran-Mantel-Haenszel analyses and differences in response rate after multiple imputation. As a general explanation, a Cochran-Mantel-Haenszel method can combine comparisons across strata while accounting for the stratification used in an analysis. The registry does not identify the specific strata in the registry record. Multiple imputation is a general approach for addressing missing outcome information by creating completed datasets under a model and combining the results; the registry labels the reported analysis as after multiple imputation, but details of the imputation model and assumptions are not reported in the registry record.

Risk differences and odds ratios or risk ratios describe different aspects of a binary comparison. A risk difference is an absolute contrast in response proportions; a ratio compares relative response levels. These measures can convey different impressions when baseline response proportions are low. Interpretation should consider the actual group proportions and their uncertainty, rather than relying on a relative measure alone. The registry’s sponsor analyses emphasize adjusted response-rate differences, while the simple re-calculations provide unadjusted contrasts.

What do p-values and intervals mean?

As a general statistical explanation, a p-value evaluates how compatible the observed data are with a specified null hypothesis, given the analysis assumptions. It does not measure the size or importance of an effect, and it is not the probability that the null hypothesis is true. A confidence interval gives a range of effect values reasonably compatible with the data and method at the stated confidence level. Its width reflects statistical precision: narrower intervals indicate less sampling uncertainty under the method, while wider intervals leave more values plausible.

The primary sponsor result reports a 95% confidence interval. The secondary sponsor analyses also report 95% confidence intervals. The posted unadjusted p-values and sponsor p-values do not necessarily answer precisely the same inferential question because their methods differ. The unadjusted re-calculations should not be treated as a substitute for prespecified, model-based trial analyses.

Why does dispersion matter?

As a general concept, dispersion describes how much participant outcomes vary around a group mean or response probability. Greater variability can make a mean difference harder to estimate precisely with a given amount of information. In count-like outcomes, the variance may not follow the assumptions of a simple normal model, particularly when observations are clustered or more variable than expected. Over-dispersion means variability exceeds what a chosen model allows; if ignored, standard errors can be too small and intervals too narrow. The primary outcome is reported as a mean with standard deviation, but the registry does not report a separate over-dispersion assessment or details of residual diagnostics.

All statistical methods depend on assumptions about the outcome, model, and missing data. The registry names the analysis methods and gives estimates, confidence intervals, and p-values, but detailed diagnostics, covariate lists, and full analysis specifications are not reported in the registry record. The results should be read with that level of methodological detail in mind.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is a difference in least squares means of -1.91 days, with a 95% confidence interval from -2.97 to -0.84. This interval gives a range of values compatible with the sponsor’s ANCOVA and its assumptions. Because it does not include zero, it is consistent with a difference between the groups under that analysis. The interval is not a range of individual participant outcomes, and it does not show that every participant experienced a change of this size.

The simple unadjusted re-calculation estimates a mean difference of -1.87 days. The posted group standard deviations are 5.259 for weekly CC-93538 and 5.075 for placebo. The outcome variability is substantial relative to the difference in group means, which is one reason to attend to the confidence interval and model-based estimate rather than treating the point estimate as exact. The sponsor’s interval is the reported trial interval; a confidence interval for the unadjusted re-calculation is not needed to understand that distinction.

The Week 24 sponsor analysis reports a response-rate difference of 40.0 percentage points for the histology threshold below 15 per high-power field, with a 95% confidence interval from 33.3 to 46.7. At Week 48, the sponsor reports adjusted response-rate differences of 18.4 percentage points and 17.0 percentage points for the two maintenance comparisons at the threshold of at most 6 per high-power field. Their respective 95% confidence intervals are 11.3 to 25.5 and 10.1 to 24.0. These intervals indicate uncertainty around adjusted group contrasts, not uncertainty around each group’s observed percentage.

Confidence intervals describe precision under the analysis used. They do not address every source of uncertainty, such as missing-data assumptions, measurement limitations, or whether the analysis was selected from many possible comparisons. The registry does not report a clinically meaningful threshold for the primary outcome. Statistical precision therefore cannot alone settle the practical importance of the estimated symptom difference.

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 sample-size illustrations use the observed effect as a planning reference and show scenarios for detecting the full observed effect, 75% of it, or 50% of it. For these continuous and binary outcomes, the figures refer to participants per arm, not a total across arms. The registry’s convention is that time-to-event illustrations give total events, but the outcomes addressed by these calculations are not time-to-event outcomes.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each illustration targets an effect equal to the stated fraction of the observed effect. The figures are calculations based on these assumptions, not the trial’s own design justification. The trial’s original sample-size assumptions and justification are not reported in the registry record.

The 80% power column indicates the illustrated number of participants per arm for an analysis to have an 80% chance of detecting the assumed effect if that effect and the planning assumptions hold. The 90% power column gives the corresponding planning target for a 90% chance. These are design concepts, not guarantees about a future study’s result. The required number rises as the target effect becomes smaller: detecting a smaller fraction of the observed effect requires more participants per arm under the same planning framework.

These figures are planning illustrations, not observed power. They do not report the probability that the completed trial detected an effect, and they do not replace the study’s reported estimates and confidence intervals. They also do not incorporate any trial-specific allowances unless those are stated in the registry record; such allowances are not reported.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -1.870; pooled standard deviation σ = 5.197.
2. n = 2 × (1.96 + 0.842)² × 5.197² / -1.870² = 121.2, rounded up to 122 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
delta <- -1.87                      # observed difference in means
sigma <- 5.19651685825232                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(4753697)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 122 (80% power), 163 (90% power)
 75% of observed effect: n per arm = 216 (80% power), 289 (90% power)
 50% of observed effect: n per arm = 485 (80% power), 650 (90% power)
power.t.test: 122.2 
Simulated power at n = 122 per arm: 0.803 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis is ANCOVA, reporting a difference in least squares means of -1.91 days, a 95% confidence interval from -2.97 to -0.84, and p < 0.001. The simple unadjusted re-calculation from the posted group means is -1.87 days. These estimates are close in direction and magnitude, but they are not identical because one is an unadjusted summary-statistic comparison and the other is a model-based adjusted result. The registry’s discrepancy indicator is false.

For secondary binary outcomes, the sponsor reports Cochran-Mantel-Haenszel differences in response rate after multiple imputation. The re-calculations instead use the posted counts and denominators to form unadjusted contrasts. The two approaches can differ because adjustment, stratification, and missing-data handling affect the estimate. The registry does not provide enough detail to recreate those sponsor analyses from the summary figures alone.

The sponsor’s own analysis takes precedence if the registry flags a discrepancy between it and a re-calculation. No such discrepancy is flagged for this trial. In all cases, the reported sponsor analysis is the primary record of the trial’s specified statistical result; the re-calculation is a transparent, unadjusted cross-check, not a competing replacement.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists many outcomes and analyses, but a multiplicity strategy is not reported in the registry record. Multiplicity concerns arise when several hypotheses are tested: even if no real effects exist, the chance of at least one small p-value can increase as the number of tests grows. Statistical procedures can control that risk, for example by adjusting significance thresholds or specifying an ordered testing hierarchy. The registry record does not state whether such a procedure was used for the posted secondary outcomes.

Accordingly, the sponsor-reported secondary p-values and the unadjusted re-calculated p-values should not be read as if each were the sole confirmatory test. The primary outcome is clearly identified, but the full prespecified testing sequence, allocation of error across endpoints, and any confirmatory status for secondary endpoints are not reported in the registry record. This limits how strongly the secondary findings can be interpreted as confirmatory evidence.

The primary population is described as Intent-to-Treat: all randomized participants are analyzed according to randomized group, regardless of whether they received CC-93538 or placebo. The outcome description also says that participants with observed values at the specified timepoint are included. The further details of how missing primary outcome values were handled are not reported in the registry record. The sponsor’s binary outcome analyses are labeled as using multiple imputation, but the imputation model, assumptions, and sensitivity analyses are not reported in the registry record.

Missingness can matter when participants without observed outcomes differ from those with observed outcomes. As a general statistical point, imputation methods rely on assumptions about the relationship between observed information and missing values. The registry does not report enough detail to assess those assumptions or determine how sensitive the results are to alternative missing-data scenarios. No interim analyses or related stopping rules are reported in the registry record. These reporting gaps do not negate the posted findings, but they limit a complete assessment of the planned inferential framework.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: appendicitis (1.4%), eosinophilic oesophagitis (1.2%), myocardial infarction (0.9%), complication associated with device (0.9%), urinary tract infection (0.9%).

The registry reports serious adverse events for three groups: CC-93538 360 mg once weekly, CC-93538 360 mg once every other week, and placebo. The numbers at risk for the serious-adverse-event summaries were 167, 117, and 143, respectively. Serious adverse events were reported for 4 participants in each CC-93538 group and 8 participants in the placebo group. No deaths were reported in any of the three groups.

These are descriptive counts from the posted safety summaries. They do not establish whether an event was caused by study treatment, and the registry record does not report a causal assessment in the registry record listed. The top listed serious-event terms include appendicitis at 1.4%, eosinophilic oesophagitis at 1.2%, myocardial infarction at 0.9%, complication associated with device at 0.9%, urinary tract infection at 0.9%, and traumatic haematoma at 0.9%. The registry does not specify in the registry record listed whether these terms are ranked across all groups or provide group-specific counts for each term.

Serious adverse events are not the same as all adverse events. The separate all-adverse-event counts are 103, 73, and 69 among the groups at risk of 167, 117, and 143, respectively. Counts alone do not account for duration of exposure or event severity beyond the registry’s classification. The safety summaries should therefore be read as reported event counts, not as a complete comparative safety assessment.

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

The results describe a randomized comparison of weekly CC-93538 with placebo during the induction period for the primary dysphagia-days endpoint. The posted arm means both decreased from baseline, and the sponsor’s adjusted analysis estimates a greater mean decrease in the CC-93538 group. Its 95% confidence interval excludes zero, while the simple unadjusted re-calculation is similar in direction and size. The registry also reports higher proportions meeting the specified histology thresholds in active-treatment groups than in placebo at the posted assessment times.

These findings do not say that every participant experienced a decrease in dysphagia days or met a histology threshold. Group means and percentages describe distributions across participants; individuals can have outcomes that differ from the group average. Nor do the results establish a particular magnitude of benefit that participants would consider important. A clinically meaningful change threshold for the primary outcome is not reported in the registry record.

The Week 48 results reflect a study sequence that included the preceding induction phase and then one of two maintenance dosing schedules. They do not isolate a maintenance-only effect, nor do the reported placebo comparisons establish which active maintenance schedule is preferable. The sponsor’s analyses and simple unadjusted re-calculations also answer somewhat different statistical questions.

Statistical significance does not establish clinical importance, safety for a particular individual, or effects in people outside the studied adult and adolescent population. The serious adverse-event summaries are descriptive and do not establish causation. The registry’s missing-data details, multiplicity procedures, and full statistical specifications are not reported, which limits a complete appraisal of uncertainty. The results should be understood as group-level evidence within this completed trial, not as a prediction for every person or a basis for individual medical decisions.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definition matters. The primary outcome is not simply a count of diary entries marked as symptomatic: it uses specified swallowing-related diary questions, a defined 14-day window, and normalization based on measurable diary days. Those rules determine what the outcome means and which records contribute to its calculation. The scale of 0 to 14 days also makes the estimated mean difference interpretable in the same units as the symptom measure.

It also shows the distinction between a raw contrast and an adjusted analysis. The simple summary-statistic re-calculation and the sponsor’s ANCOVA estimate are similar, but they arise from different methods. Reporting both helps readers distinguish transparent arithmetic from the trial’s model-based result. The same distinction applies to the secondary binary outcomes: unadjusted proportions and contrasts are not interchangeable with sponsor analyses after stratification and multiple imputation.

The trial’s primary symptom measure and secondary histology endpoints provide complementary perspectives, but they are not duplicates. A statistical pattern across both types of outcome can add context, while differences in timepoint, threshold, and analysis method prevent treating them as a single result. The registry’s lack of a reported multiplicity strategy is particularly relevant when interpreting a large set of secondary analyses.

Finally, the record demonstrates that a completed trial can have interpretable headline estimates while still leaving key design and analysis details unreported. The original sample-size rationale, full model specifications, missing-data assumptions, and multiplicity handling are not reported in the registry record. These omissions do not change the posted numerical results, but they shape how confidently readers can assess their planning, robustness, and confirmatory status.

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.

Several limitations are specific to the information reported for this trial. The primary endpoint relies on diary responses, and the registry defines a measurable diary day but does not report further rules for incomplete diaries or the detailed handling of missing Week 24 outcomes. The posted primary group means are based on observed values at the specified timepoint, while the complete pattern of missingness is not reported in the registry record.

The full ANCOVA specification is not reported, including the covariates and diagnostic checks. The sponsor’s analysis can therefore be described from its reported method and estimate, but it cannot be independently reconstructed in detail from the record. Similarly, the binary sponsor analyses are labeled as Cochran-Mantel-Haenszel after multiple imputation, but the strata and imputation assumptions are not reported in the registry record listed.

The registry lists many outcome measures and analyses without reporting a multiplicity adjustment or testing hierarchy. This is important when weighing secondary findings. The Week 48 histology summaries reflect participants with reported outcomes at that timepoint, and the information listed does not establish that the maintenance comparisons are free from bias due to missing observations or selection into follow-up.

The primary outcome is a symptom measure and the secondary outcomes include histology thresholds, but the registry does not report a clinically meaningful threshold for the primary mean change. The record also does not provide subgroup results, detailed exposure-adjusted safety rates, or a causal assessment of the listed serious adverse events in the registry record. These limitations concern the scope and detail of the registry record; they do not establish that the underlying trial lacked analyses or procedures that are not reported there.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy and Safety of CC-93538 in Adult and Adolescent Participants With Eosinophilic Esophagitis — NCT04753697.
• Registry record last updated 2025-03-13; status last verified 2025-02.
• Results first posted 2025-03-13.
• 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

NCT04753697 is a completed Phase 3 randomized, double-blind, placebo-controlled parallel-group study of CC-93538 in adults and adolescents with eosinophilic esophagitis. The study included a 24-week induction phase followed by a 24-week maintenance phase, with weekly and every-other-week CC-93538 maintenance strategies and a placebo group.

The primary endpoint was change from baseline in mean dysphagia days at Week 24. The sponsor reported an ANCOVA difference in least squares means of -1.91 days, with a 95% confidence interval from -2.97 to -0.84 and p < 0.001. The registry also reports secondary histology comparisons and descriptive serious adverse-event counts, including no deaths in the listed groups.

The registry record does not report the original sample-size justification, detailed missing-data assumptions, or a multiplicity strategy. The findings are group-level estimates from the posted analyses and should be interpreted with those reporting limitations in view.