A Study to Evaluate the Efficacy and Safety of CC-93538 in Adult and Adolescent Japanese Participants With Eosinophilic Gastroenteritis: 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 Japanese Participants With Eosinophilic Gastroenteritis (NCT05214768), a randomized phase 3 study. The primary outcome is Change From Baseline in Mean Number of Peak Eosinophils (Eos) Count Per High-power Field (Hpf) in Gastrointestinal (GI) Biopsies.

2. Clinical Question

The clinical question combines a tissue-based measure with a randomized treatment comparison. The endpoint concerns eosinophil counts in gastrointestinal biopsy specimens, rather than a symptom score alone. The study also listed clinical and histologic response measures, symptom-domain measures, and later biopsy outcomes as secondary outcomes. Those outcomes can add context, but they do not replace the primary Week 16 comparison.

The registry record identifies the condition as eosinophilic gastroenteritis and describes the study purpose as evaluating the safety and efficacy of CC-93538 in adult and adolescent participants. It does not provide arm descriptions beyond the treatment labels for the primary induction comparison. Further details about eligibility criteria and the clinical rationale for selecting this endpoint are not reported in the registry record.

3. Trial Design

The registry describes a Phase 3, multicenter, randomized, double-blind, placebo-controlled study with induction and maintenance phases. Its design is parallel-group, and the masking classification is quadruple. The listed interventions are CC-93538 and placebo. The primary endpoint compares the CC-93538 360 mg once-weekly group with placebo at Week 16.

Enrollment was 48, and the registry status is completed. The study start date is 2022-03-04, and the primary completion date is 2024-07-02. These record details describe the trial’s overall conduct, while the primary endpoint analysis includes 30 participants in the CC-93538 arm and 16 in the placebo arm. The registry’s population description says that all randomized participants belong to the intent-to-treat population regardless of whether they received investigational product, but only participants analyzed at the specified timepoint are included in the endpoint analysis.

The title and outcome list indicate that the study included induction and maintenance assessments. The secondary outcomes include Week 16 and Week 48 measures, as well as a Week 48 biopsy outcome. The record also lists a maintenance dosing group described as CC-93538 360 QW/Q2W in a secondary analysis. The full treatment schedule, allocation ratio, and details of how participants moved between phases are not reported in the registry record.

Randomization helps make treatment groups comparable in expectation, while masking is intended to reduce the influence of treatment knowledge on participant care, assessment, and reporting. Those are general features of trial design; the registry’s design labels do not establish how well these aims were achieved in practice. The record does not report the randomization procedure, the specific parties included in the quadruple masking, or the original sample-size justification.

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.

Induction Period

Reasons for not completing this period:

Maintenance Period

Reasons for not completing this period:

Open Label Extension Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population which consists of all randomized participants regardless of whether or not the participant received IP (CC-93538 or placebo). Only participants analyzed at 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 Number of Peak Eosinophils (Eos) Count Per High-power Field (Hpf) in Gastrointestinal (GI) Biopsies, measured over Baseline and Week 16.

The primary endpoint measures change from baseline in the mean number of peak eosinophils counted per high-power field in gastrointestinal biopsies, with baseline and Week 16 as the stated timeframe. A lower follow-up count relative to baseline is represented by a negative change, while a positive change represents an increase. The arm estimates reported for this endpoint are least-squares means, a model-based way to estimate group means while accounting for terms in the analysis model.

Biopsy eosinophil counts provide a tissue-based measure of disease activity. That makes the endpoint relevant to a study assessing eosinophilic gastroenteritis, where the presence of eosinophils in gastrointestinal tissue is part of the disease being studied. This is a general explanation of why such a measure may be used; the registry does not state the specific rationale for choosing it as the primary endpoint.

The endpoint description contains a wording inconsistency: its title refers to counts in gastrointestinal biopsies, while the description says blood samples were collected to assess eosinophil count. The record does not clarify that inconsistency. The endpoint unit is the peak number of eosinophils counted per field. The registry defines baseline as the last measurement collected on or before the first dose for the induction phase.

A change score captures movement from each participant’s baseline rather than just a Week 16 value. The between-group contrast then addresses whether the average change differed between assigned groups. The primary result is not, on its own, a complete account of symptoms, function, safety, or longer-term outcomes.

7. Results Posted in the Registry

• CC-93538 360 mg QW: mean -100.40 versus 122.80 on control; difference -223.20 (95% CI -369.72 to -76.68), standardized effect d = -0.92; z-test p = 0.003.

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.

Induction Phase: Percentage of Participants Who Achieve Both Clinical and Histologic Response Composite at Week 16

• 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:
  • CC-93538 360 mg QW: 6.2% (2/32) versus 0.0% (0/16) on control; risk difference 6.2 percentage points (95% CI -2.1 to 14.6); unadjusted two-proportion z-test p = 0.307.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CC-93538 360 mg QW and the control. The interval gives the range of effects that remain compatible with the data.

Induction + Maintenance: Change From Baseline in Mean Number of Peak Eosinophils (Eos) Count Per High-power Field (Hpf) in Gastrointestinal (GI) Biopsies at Week 48

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • CC-93538 360 mg QW: mean -24.10 versus 98.60 on control; difference -122.70 (95% CI -299.24 to 53.84), standardized effect d = -0.47; z-test p = 0.173.
  • CC-93538 360 QW/Q2W: mean -151.20 versus 98.60 on control; difference -249.80 (95% CI -468.11 to -31.49), standardized effect d = -0.94; z-test p = 0.025.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CC-93538 360 mg QW and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for CC-93538 360 QW/Q2W than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Induction Phase: Percent Changes in Mean Number of Peak Eos Per Hpf in GI Biopsies From Baseline

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • CC-93538 360 mg QW: mean -13.40 versus 61.60 on control; difference -75.00 (95% CI -132.05 to -17.95), standardized effect d = -0.76; z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for CC-93538 360 mg QW than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several dimensions: symptom-domain scores, a combined clinical and histologic response, biopsy eosinophil counts and percentage changes, and a histologic response threshold. Some are assessed at Week 16 and others at Week 48. Taken together, they broaden the evidence beyond the primary Week 16 count-change endpoint, but they do not represent one single construct or analysis population.

The posted secondary findings are mixed in their statistical strength and in the amount of information available for each measure. Some comparisons have intervals that include no difference, while others have intervals that do not; several secondary outcomes have no reported sponsor analysis in the registry entry. This variation means the secondary results should be viewed as contextual rather than as a uniform confirmation of the primary result. Their differing endpoints and timepoints also mean they should not be expected to match the primary result exactly.

The clinical and histologic composite asks a distinct question from a mean change in biopsy counts. Symptom scores likewise assess participant-reported domains rather than tissue counts alone. Later maintenance outcomes address a different time horizon and, in one analysis, include more than one CC-93538 dosing group. Differences in endpoint definition, analysis count, and treatment phase affect how directly those results can be compared with the primary Week 16 contrast.

Unadjusted secondary results carry less weight when many outcomes are tested and the registry does not report a multiplicity procedure. As a general statistical matter, examining numerous endpoints without controlling the family of tests makes chance findings more likely. The record does not establish whether a hierarchy or adjustment was prespecified. Secondary results can therefore help identify patterns for further study, but isolated nominal p-values should not be treated as definitive evidence or as replacements for the primary analysis.

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

• Induction Phase: Changes in Each of 5 Domain Scores of the Izumo Scale From Baseline at Week 16
• Induction + Maintenance: Changes in Each of 5 Domain Scores of the Izumo Scale From Baseline at Week 48
• Induction Phase: Percentage of Participants Who Achieve Both Clinical and Histologic Response Composite at Week 16
• Induction + Maintenance: Percentage of Participants Who Achieve Both Clinical and Histologic Response Composite at Week 48
• Induction + Maintenance: Change From Baseline in Mean Number of Peak Eosinophils (Eos) Count Per High-power Field (Hpf) in Gastrointestinal (GI) Biopsies at Week 48
• Induction Phase: Percent Changes in Mean Number of Peak Eos Per Hpf in GI Biopsies From Baseline
• Induction + Maintenance: Percent Changes in Mean Number of Peak Eos Per Hpf in GI Biopsies From Baseline
• Induction Phase: Percentage of Participants With Eosinophil Histologic Response (> 75% Reduction)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary analysis is reported as an analysis of covariance (ANCOVA), with the result expressed as a least-squares mean difference. ANCOVA is a general statistical method for comparing group outcomes while adjusting for variables included in the model. In a randomized trial, adjustment can account for prespecified baseline measures or other model terms and can improve precision when those terms are informative. The registry record does not report the full model specification, the covariates included, or the assumptions used for the primary ANCOVA.

A least-squares mean is a model-based group estimate rather than simply the arithmetic average of the observed values. The reported arm estimates are -100.4 for CC-93538 and 122.8 for placebo. The reported least-squares mean difference is -223.2. Because the registry does not fully describe the model, readers should rely on the reported ANCOVA analysis for the trial’s primary inferential result rather than attempting to reconstruct every part of it from the arm summaries.

What does the confidence interval express?

A confidence interval describes uncertainty around an estimated effect under the statistical model and its assumptions. In repeated use of the same procedure, intervals constructed this way would cover the underlying effect at the stated rate. For this primary result, the registry reports a 95% confidence interval from -370.2 to -76.3. The interval represents values compatible with the data and model at that confidence level; it is not a guarantee that the true effect lies within those endpoints, nor does it assign a probability to a particular value after the data have been observed.

The registry also reports p = 0.003. A p-value is calculated under a null hypothesis, commonly that there is no treatment-group difference. It describes how unusual data at least as incompatible with that null hypothesis would be if the null and model assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the clinical importance of the result. Interpretation is stronger when the estimate, interval, endpoint, and design are considered together rather than relying on the p-value alone.

What is the recalculation?

The recalculated comparison uses the posted group summaries to form a simple, unadjusted contrast. Its estimated mean difference is -223.2, and its approximate confidence interval is -369.7 to -76.68, with p = 0.003. This approach is intentionally simpler than the sponsor’s ANCOVA analysis. It does not reproduce the model’s adjustment or any unreported analysis details. Its purpose is to provide a summary-statistic cross-check, not to claim that the original analysis was a simple comparison.

The recalculation uses standard errors reported for the two arm estimates and an approximate pooled standard deviation. A standard error describes the uncertainty in an estimated mean, whereas a standard deviation describes variation among measurements. They answer different questions. The summary-statistic recalculation is approximate because the reported information does not fully specify participant-level variability or the primary model. The sponsor’s own reported analysis remains the direct record of the trial’s primary analysis.

Why can over-dispersion matter?

For count outcomes, a basic statistical model may assume that the variability is tied closely to the mean. Over-dispersion means that the observed variability is greater than such a model expects. As a general statistical matter, failing to account for over-dispersion can make standard errors too small and confidence intervals too narrow, leading to overstated precision. The registry record does not report whether over-dispersion was assessed or how the primary analysis handled the distribution of biopsy counts. The endpoint is reported as a least-squares mean change, so readers should not assume a particular count-model approach that is not described.

The registry’s primary population is described as intent-to-treat, including all randomized participants regardless of whether they received investigational product. It then qualifies that only participants analyzed at the specified timepoint are included. These statements identify the intended population concept and the timepoint analysis set, but they do not specify how missing Week 16 measurements were handled. Imputation methods, sensitivity analyses, and reasons for missing data are not reported in the registry record.

Randomization is intended to balance measured and unmeasured prognostic factors across groups in expectation. Masking can reduce the influence of treatment expectations on assessments and behavior. These general principles support interpretation of a randomized, masked comparison, but the record does not report implementation details or whether masking was maintained. The allocation procedure and any stratification factors are also not reported in the registry record.

Multiplicity arises when many outcomes or comparisons are tested. If each is assessed without adjustment, the chance of at least one small p-value across the collection of tests can increase. General approaches include prespecified testing hierarchies or adjustments to the significance threshold, but no multiplicity procedure is reported in the registry record. This matters particularly for interpreting secondary results: an isolated nominal p-value is weaker evidence when many outcomes are assessed and the testing plan is unknown.

The primary analysis reports an ANCOVA estimate and inferential statistics, but the full statistical analysis plan is not reported in the registry record. This includes details such as model covariates, missing-data rules, assumption checks, and any planned sensitivity analyses. The posted result can therefore be described accurately, while some aspects of the analysis cannot be independently reconstructed from the registry entry.

11. Confidence Intervals and Precision

The primary estimate is -223.2, with a reported 95% confidence interval from -370.2 to -76.3. The interval shows that the estimate is not known with exact precision: values across that range are compatible with the registry’s ANCOVA analysis at the stated confidence level. Because the interval lies below zero, the reported analysis supports a negative between-group contrast for change in the biopsy count measure.

The recalculated unadjusted interval is -369.7 to -76.68. It is close to, but not identical with, the registry interval. The distinction reflects different analytical approaches and the limited detail available for reproducing the adjusted model. The recalculated interval should be read as an approximate check based on group summaries, not as a second sponsor-reported interval.

Precision depends on the variability of the outcome, the number of participants analyzed, and the analysis model. In general, more information can narrow an interval, while greater variability can widen it. The primary endpoint analysis includes 30 participants in the CC-93538 arm and 16 in the placebo arm, so the estimate rests on the available analysis set rather than all enrollment. The registry does not report a detailed account of why the endpoint analysis counts differ from enrollment.

A confidence interval concerns statistical uncertainty, not clinical importance. The endpoint is a peak eosinophil count per high-power field, and the registry does not give a threshold for a clinically meaningful difference on this measure. Nor does the interval capture uncertainty about unreported features such as missing-data assumptions or model specification. It is best interpreted with the endpoint definition and analysis method in view.

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 figures are planning illustrations based on the observed effect, not the trial’s original design calculations. For this continuous primary endpoint, the figures are participants per arm, not total event counts. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row considers an effect to detect expressed as a fraction of the observed effect.

For planning at 100% of the observed effect, the illustration gives 19 participants per arm for 80% power and 25 participants per arm for 90% power. At 75% of the observed effect, the figures are 33 participants per arm for 80% power and 44 participants per arm for 90% power. At 50% of the observed effect, they are 74 participants per arm for 80% power and 99 participants per arm for 90% power.

Power is the probability that a specified statistical test will reject its null hypothesis under a particular assumed effect and model. The 80% and 90% columns therefore describe different target probabilities of detecting the assumed effect, if the planning assumptions hold. The higher target generally requires more participants. Smaller assumed effects also need more participants, because a subtler difference is harder to distinguish from random variation.

The curve should be read as the same planning relationship across assumed effect sizes: as the target effect becomes smaller, the required participants per arm rise. These calculations do not establish what the trial’s original designers planned, because the original sample-size justification and assumptions are not reported in the registry record. This is not observed power; it is a forward-looking planning illustration constructed from the observed effect and stated assumptions.

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 = -223.200; pooled standard deviation σ = 241.857.
2. n = 2 × (1.96 + 0.842)² × 241.857² / -223.200² = 18.4, rounded up to 19 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 <- -223.2                      # observed difference in means
sigma <- 241.85684716941                     # 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(5214768)
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 = 19 (80% power), 25 (90% power)
 75% of observed effect: n per arm = 33 (80% power), 44 (90% power)
 50% of observed effect: n per arm = 74 (80% power), 99 (90% power)
power.t.test: 19.4 
Simulated power at n = 19 per arm: 0.794 (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 registry’s own primary analysis is an ANCOVA, reported as a least-squares mean difference of -223.2, with a 95% confidence interval from -370.2 to -76.3 and p = 0.003. That is the trial’s reported inferential analysis and should be distinguished from the unadjusted recalculation based on posted summary statistics.

The recalculation gives the same estimated difference, -223.2, and the same p-value, 0.003. Its approximate confidence interval, -369.7 to -76.68, is close to the reported interval but has slightly different limits. The recalculation does not have the full ANCOVA model specification and cannot reproduce its adjustments. It serves as a simple check on the direction and broad scale of the reported result, not as an independent trial analysis.

The registry reports no discrepancy between the posted result and the recalculation. Even so, their methods are not interchangeable. The sponsor’s reported ANCOVA remains the source for the trial’s primary analysis, while the summary-statistic comparison is useful for understanding how the posted group estimates relate to the contrast.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 27 outcome measures and reports 26 secondary outcomes, alongside the primary endpoint. Testing multiple outcomes creates a multiplicity concern: when many hypotheses are examined, the chance of obtaining at least one apparently strong result by chance can rise. This is a general statistical issue and does not mean that any particular reported result is false.

Possible strategies include specifying a hierarchy of tests, allocating error rates across outcomes, or labeling some analyses exploratory. The registry record does not report a multiplicity adjustment, testing hierarchy, or other plan for controlling the overall false-positive risk. Without that information, secondary p-values should be interpreted cautiously, especially when considering a collection of endpoints together.

The registry describes the primary population as intent-to-treat, defined as all randomized participants regardless of whether they received study product. It also says that only participants analyzed at the specified timepoint are included. The primary endpoint counts are 30 for CC-93538 and 16 for placebo, while other endpoint analyses use different numbers of participants. The record does not explain all differences in analysis counts or state how missing measurements were treated.

Missing data can affect both the estimated effect and its precision. As a general matter, the implications depend on why data are missing and on the assumptions and methods used to address them. Common approaches include analyzing available measurements or using imputation, but the registry does not identify which missing-data methods were used for the primary endpoint, whether sensitivity analyses were conducted, or whether missingness differed by group. Those details are not reported in the registry record.

The primary analysis is identified as ANCOVA, but the full model specification, covariates, assumption checks, and analysis plan are not reported in the registry record. The available entry therefore permits a description of the reported estimate and its uncertainty, but not a complete audit of multiplicity control, missing-data handling, or every modeling decision.

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: intervertebral disc protrusion (8.3%), cataract (2.3%), gastroenteritis (2.3%), pilonidal disease (2.3%), respiratory tract infection (2.3%).

The registry lists serious adverse event counts in four phase-specific groups. In the induction and maintenance CC-93538 360 mg QW group, 20 participants were at risk and 0 were reported with serious adverse events. In the maintenance CC-93538 360 mg QW/Q2W group, 12 were at risk and 1 was reported with a serious adverse event. In the induction and maintenance placebo group, 16 were at risk and 0 were reported with serious adverse events. In the open-label long-term extension CC-93538 group, 44 were at risk and 7 were reported with serious adverse events.

These are counts for differently labeled study phases and groups, not a single direct comparison of randomized treatments over a common follow-up period. In particular, the open-label extension is distinct from the induction and maintenance randomized groups. The serious event terms listed in the registry include intervertebral disc protrusion at 8.3%, and cataract, gastroenteritis, pilonidal disease, respiratory tract infection, and sacroiliitis at 2.3% each. The record does not provide enough context in this listing to interpret those term percentages as comparative risks.

No deaths were reported in any of the four listed groups. Serious adverse event counts alone do not describe all adverse experiences, their duration, severity, or relationship to treatment. The registry also lists other adverse events separately, but those counts should not be confused with serious adverse events.

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

The primary result describes a group-level difference in change from baseline in peak eosinophil counts in gastrointestinal biopsies at Week 16. The registry’s ANCOVA estimate is -223.2, with a 95% confidence interval from -370.2 to -76.3 and p = 0.003. This indicates that the estimated change was lower in the CC-93538 group than in the placebo group on the specified measure.

The result does not, by itself, establish how large a change is clinically meaningful. The registry does not give a clinically important difference threshold for this endpoint, and a difference in a tissue count is not the same as a direct measure of symptoms or daily functioning. The study also reports other outcomes that address different aspects of the condition, but those results require separate interpretation and do not automatically validate or invalidate the primary finding.

The result does not establish an individual participant’s likely outcome. Group estimates summarize averages and do not show how much participants’ responses varied beyond the reported uncertainty. Nor does the primary endpoint establish whether any difference persists through maintenance or later follow-up. Week 48 outcomes are separate measures and use their own analysis counts and comparisons.

Statistical evidence and treatment decisions are distinct matters. A p-value does not measure the probability that a treatment is beneficial, and a confidence interval does not indicate the probability that an individual will experience a particular result. The primary analysis should be considered together with the study’s population, the endpoint’s meaning, the secondary results, and the safety information. The registry record alone does not resolve the clinical importance or broader applicability of the findings.

18. Why This Trial Matters Statistically

This trial illustrates why the analysis population and the reported endpoint counts matter. Overall enrollment was 48, while the primary analysis includes 30 participants in the CC-93538 arm and 16 in the placebo arm. The registry’s intent-to-treat description is qualified by inclusion only of participants analyzed at the specified timepoint. Readers need both pieces of information to understand which participants contribute to the posted estimate.

It also provides a useful distinction between a sponsor-reported model-based analysis and a simple recalculation from group summaries. Both yield an estimated difference of -223.2 and p = 0.003, while the confidence interval limits differ slightly. That comparison shows how a summary-statistic check can support an understanding of direction and approximate magnitude without reproducing the full adjusted analysis.

The endpoint itself highlights that trial results are tied to measurement choices. A Week 16 biopsy count is not interchangeable with symptom scores, a composite response, or a later maintenance measure. Multiple outcome types can enrich the evidence, but they also raise questions about multiplicity, analysis counts, and which comparisons were prespecified.

Finally, the record exposes important limits on registry-based interpretation. The primary model details, missing-data methods, multiplicity plan, and original sample-size assumptions are not reported in the registry record. Recognizing those gaps is part of sound statistical reading: it allows the posted estimate to be described precisely without claiming more than its analysis and documentation can support.

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.

The primary analysis rests on 30 participants in the CC-93538 group and 16 in the placebo group, compared with overall enrollment of 48. The registry does not explain the difference between enrollment and the endpoint analysis counts. Smaller analysis groups generally provide less information than larger ones, and differences in who contributes data can affect how representative an estimate is of all randomized participants.

The endpoint description is internally inconsistent: the title refers to gastrointestinal biopsy counts, while the description says blood samples were collected to assess eosinophil count. The registry does not resolve whether this is a wording error or describes an additional measurement. This limits certainty about the measurement details available from the record.

The full statistical analysis plan is not reported in the registry record. The ANCOVA covariates and model specification, missing-data procedures, sensitivity analyses, assumption checks, and multiplicity strategy are not described. These omissions prevent a complete independent reconstruction of the primary analysis or a full assessment of the secondary testing program.

The record lists multiple outcomes across different timepoints and phases, with varying participant counts. Results from these measures cannot be treated as direct replications of the primary endpoint because they assess different constructs or treatment periods. Secondary inferential results are also harder to weigh when the registry does not report whether adjustments for multiple testing were applied.

Safety groups span induction, maintenance, and an open-label extension, so their counts do not form a single comparable randomized contrast. The registry gives serious event counts and selected event terms but not the detailed case information or common follow-up context needed for a fuller comparative safety interpretation. The original sample-size assumptions and justification are also not reported in the registry record.

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 Japanese Participants With Eosinophilic Gastroenteritis — NCT05214768.
• Registry record last updated 2026-09-14; status last verified 2026-08.
• Results first posted 2025-09-18.
• 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

NCT05214768 is a completed Phase 3, multicenter, randomized, double-blind, placebo-controlled parallel study of CC-93538 in adults and adolescents in Japan with eosinophilic gastroenteritis. Overall enrollment was 48. The primary endpoint was change from baseline to Week 16 in mean peak eosinophils per high-power field in gastrointestinal biopsies.

The registry reports an ANCOVA least-squares mean difference of -223.2 for CC-93538 versus placebo, with a 95% confidence interval from -370.2 to -76.3 and p = 0.003. The primary analysis included 30 participants in the CC-93538 group and 16 in the placebo group. The record lists a range of secondary clinical and histologic outcomes and serious adverse event counts across treatment phases.

The full analysis plan, missing-data methods, multiplicity approach, and original sample-size justification are not reported in the registry record. These limits matter when interpreting secondary results and assessing how fully the primary analysis can be independently reproduced.