Safety and Efficacy of Deucravacitinib in Participants With Moderate to Severe Ulcerative Colitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Deucravacitinib in Participants With Moderate to Severe Ulcerative Colitis (NCT03934216), a randomized phase 2 study. The primary outcome is Clinical Remission Response Rate at Week 12.

2. Clinical Question

3. Trial Design

This was a phase 2, randomized, double-blind, placebo-controlled study with a parallel-group model. The registry record describes masking as quadruple. The study assessed deucravacitinib, also identified in the record as BMS-986165, against placebo in participants with moderate to severe ulcerative colitis. Enrollment was 131. The trial is listed as completed, with a start date of 2019-07-01 and a primary completion date of 2021-06-13.

The primary outcome population is identified as all randomized participants. The primary outcome results list 88 participants in the treatment group and 43 in the placebo group. The reported primary outcome was the percentage meeting the clinical remission definition at week 12. Three secondary outcomes are listed: clinical response, endoscopic response, and histological improvement response at or up to week 12.

Randomization supports a comparison of assigned groups, while masking is intended to reduce the influence of knowledge about assignment on trial conduct and assessment. These design characteristics do not by themselves establish how randomization was implemented, which factors were used for stratification, or how missing observations were handled. Those details are not reported in the registry record. The trial’s original sample-size justification and its prespecified statistical analysis plan are also 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.

Before assignment: 131 Participants Randomized and 129 Treated

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All Randomized Participants

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 Clinical Remission Response Rate at Week 12, measured over From first dose to 12 weeks..

The primary endpoint is the clinical remission response rate at week 12, expressed as the percentage of participants meeting the remission criteria. The registry record defines remission using a modified Mayo score composed of stool frequency, rectal bleeding, and endoscopic subscores. The stated criteria require a stool-frequency subscore of <= 1 with at least a 1-point decrease from baseline, a rectal-bleeding subscore of 0, and an endoscopic subscore of <= 1, with friability excluded from the endoscopic assessment.

The modified Mayo score ranges from 0 to 9 points, and a score from 5 to 9 points was required for randomization under the protocol definition of moderate to severe disease. The endpoint combines symptom-related components with an endoscopic component, so it represents more than a change in a single symptom. In general, a remission endpoint is used to classify whether participants meet a defined clinical state at a specified assessment time, rather than merely recording a change in one measurement. The registry record also includes a broader remission description based on the Mayo score; the operational criteria above are the specific modified-score criteria it lists for this outcome.

The outcome is reported as a percentage, with a 95% confidence interval for each group. A percentage is useful for communicating how common the defined outcome was in each group, while the interval conveys uncertainty around that estimate.

7. Results Posted in the Registry

• Treatment: 14.8% (13/88) versus 16.3% (7/43) on control; risk difference -1.5 percentage points (95% CI -14.8 to 11.8), risk ratio 0.91 (0.39–2.11); unadjusted two-proportion z-test p = 0.822.

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.

Clinical Response Rate at 12 Weeks

• 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:
  • Treatment: 37.5% (33/88) versus 32.6% (14/43) on control; risk difference 4.9 percentage points (95% CI -12.3 to 22.2), risk ratio 1.15 (0.69–1.91); unadjusted two-proportion z-test p = 0.580.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Endoscopic Response at Week 12

• 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:
  • Treatment: 19.3% (17/88) versus 27.9% (12/43) on control; risk difference -8.6 percentage points (95% CI -24.3 to 7.2), risk ratio 0.69 (0.36–1.32); unadjusted two-proportion z-test p = 0.266.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Histological Improvement Response Rate at 12 Weeks

• 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:
  • Treatment: 21.6% (19/88) versus 16.3% (7/43) on control; risk difference 5.3 percentage points (95% CI -8.7 to 19.3), risk ratio 1.33 (0.60–2.91); unadjusted two-proportion z-test p = 0.474.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover related but distinct aspects of response: clinical response, endoscopic response, and histological improvement. Across these measures, the observed treatment-versus-placebo estimates are mixed rather than consistently favoring one group. Their confidence intervals allow for no difference, and the sponsor-reported comparisons do not establish a clear separation. This pattern does not provide an unambiguous secondary-outcome confirmation of the primary result.

These measures relate to the primary endpoint because they assess clinical status or tissue and endoscopic findings during the same general assessment period. They are not interchangeable with clinical remission: a participant can meet one outcome definition without necessarily meeting another. The registry record lists the outcomes and their week-12 timing, but does not report how the endpoint definitions relate to one another in a hierarchy or whether any were designated as key confirmatory outcomes.

In general, testing several outcomes increases the chance that at least one may appear unusual by chance, even when no underlying difference exists. This is why secondary results are often interpreted with caution unless a multiplicity strategy is prespecified and reported. No multiplicity adjustment is reported in the registry record. The individual secondary p-values and estimates can describe the posted data, but they should not be read as independent proof of efficacy or as a definitive ranking of outcomes.

The broad takeaway is that the secondary outcomes add descriptive context but do not remove the uncertainty in the primary comparison. Their different directions may reflect the fact that they measure different features of ulcerative colitis, sampling variation, or other factors. The registry results alone do not identify which explanation is most important, and the individual secondary findings should not be over-interpreted in isolation.

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

• Clinical Response Rate at 12 Weeks
• Endoscopic Response at Week 12
• Histological Improvement Response Rate at 12 Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

The outcome is binary: each participant either met the defined remission criteria at the assessment or did not. For a binary outcome, the response rate is the percentage of participants classified as having the event. The registry reports the treatment rate as 14.8% and the placebo rate as 16.3%. These percentages describe the observed groups; they are not measurements of how much an individual participant improved.

What does the risk difference mean?

The recalculated risk difference compares the two observed rates by subtracting the placebo rate from the treatment rate. The posted estimate is -0.015. A value below zero indicates that the observed event rate was lower in the treatment group on this scale; a value above zero would indicate a higher rate. The 95% confidence interval is -0.148 to 0.118. Because this interval includes zero, the data are compatible with no difference as well as with differences in either direction. The interval is an expression of statistical uncertainty, not a range that guarantees where the true value lies.

This risk difference is an unadjusted recalculation from the posted summary statistics. It treats the two groups as a direct comparison and does not incorporate any stratification or adjustment. It is therefore useful for a transparent descriptive comparison, but it need not match an analysis that accounts for design features.

Why is an odds ratio also reported?

The registry reports the sponsor’s group comparison as an odds ratio from a stratified Cochran-Mantel-Haenszel analysis. An odds ratio compares the odds of an outcome between groups, rather than comparing the percentages directly. An odds ratio of 1 represents equal odds; values on either side represent different relative odds. The reported estimate is 0.9, with a 95% confidence interval from 0.3 to 2.4. The interval is broad and includes 1, so it does not show a clear separation in odds.

The Cochran-Mantel-Haenszel approach combines information across strata. In general, stratification can account for specified grouping factors when estimating a treatment comparison. The factors used for stratification are not reported in the registry record, so their role cannot be described further. Odds ratios and risk differences are distinct effect measures; their numerical values should not be compared as if they shared the same scale.

How should the p-values be read?

A p-value describes how unusual data at least as incompatible with a specified null model would be if that model were true. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The sponsor’s primary analysis reports p = 0.594. The recalculated unadjusted comparison reports p = 0.822. These values do not provide strong evidence against a no-difference model, but they do not prove that the groups are identical. The estimates and their confidence intervals are needed to understand the direction and precision of the comparison.

In general, over-dispersion matters when observed variability exceeds what a statistical model assumes. It can make standard errors too small if ignored, which can make intervals too narrow and tests too optimistic. The registry record does not report an over-dispersion assessment for these binary outcomes, and the stated methods do not establish that over-dispersion was relevant.

What does masking contribute?

The record describes the study as quadruple masked. In general, masking can help limit bias that might arise if participants, clinicians, outcome assessors, or other trial personnel know which treatment was assigned. The registry record does not specify which four roles were masked, so it is not possible to identify them from this information. Randomization and masking strengthen the basis for a controlled comparison, but they do not eliminate uncertainty from sample size, outcome measurement, missing data, or the analysis choices used.

The record also identifies the primary outcome population as all randomized participants. This identifies the stated population for the endpoint, but the registry record does not explain the handling of participants with missing week-12 assessments or other deviations. Those details matter because binary response rates depend on how each participant is classified in the analysis.

11. Confidence Intervals and Precision

The primary group estimates are accompanied by 95% confidence intervals: 7.4% to 22.2% for treatment and 5.2% to 27.3% for placebo. The intervals overlap, and both include a range of possible response rates. Overlap alone is not a formal test of the difference between groups; the direct comparison is better represented by the risk-difference interval and the sponsor’s odds-ratio interval.

The recalculated risk-difference interval extends from -0.148 to 0.118. It includes zero and allows for a treatment rate below or above the placebo rate. This breadth indicates limited precision for the between-group effect in this trial. The sponsor’s odds-ratio interval, 0.3 to 2.4, is also broad and spans values on either side of equal odds. Both intervals therefore leave meaningful uncertainty about the size and direction of the treatment contrast.

In general, a confidence interval is a range produced by a statistical method that reflects sampling uncertainty under its assumptions. It does not account automatically for every possible source of bias, such as missing outcome data, measurement issues, or limitations in generalizability. It also does not mean that every value inside the interval is equally plausible.

The 95% confidence intervals for the primary response percentages are wide relative to the observed rates, particularly in the placebo group, which has fewer participants in the reported endpoint results. This is consistent with less stable estimates when the number of observations is limited, although the exact contribution of sample size and other factors is not separately reported. The intervals should be read alongside the effect estimates, not as proof of equivalence or proof that a clinically important difference is absent.

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 material is a planning illustration based on the observed effect, not the original trial design. For these binary outcomes, its entries are participants per arm. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is defined as a stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect is present and the calculation model applies. The 90% power column describes the corresponding planning target for a 90% chance. These are prospective planning quantities, not evidence about the probability that the completed trial detected an effect and not a measure of the observed result.

Rows labeled as planning for 100% of the observed effect use the full observed effect as the target; the 75% and 50% rows use smaller target effects. Smaller effects require more participants to distinguish them from random variation with the same planned power and significance level. For the primary outcome, the illustration lists 9,073 participants per arm for 80% power and 12,145 for 90% power when using 100% of the observed effect. The corresponding figures are 16,289 and 21,806 for planning around 75%, and 37,008 and 49,542 for planning around 50%.

The curve presents the same planning relationship visually. These figures are not observed power, and they should not be read as a claim that the completed trial had a particular probability of finding a result. They are conditional planning illustrations based on 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.163; treatment proportion p₁ = 0.148; average p̄ = 0.155.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5122 = 1.0038.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5120 = 0.4310.
4. n = (1.0038 + 0.4310)² / (-0.0151)² = 9,072.2, rounded up to 9,073 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 <- 0.162790697674419                          # control proportion
p1 <- 0.147727272727273                          # 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(3934216)
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 = 9,073 (80% power), 12,145 (90% power)
 75% of observed effect: n per arm = 16,289 (80% power), 21,806 (90% power)
 50% of observed effect: n per arm = 37,008 (80% power), 49,542 (90% power)
power.prop.test: 9072.2 
Simulated power at n = 9,073 per arm: 0.799 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports a sponsor analysis for the primary outcome using a stratified Cochran-Mantel-Haenszel method. It gives an odds ratio of 0.9, a 95% confidence interval from 0.3 to 2.4, and p = 0.594. The recalculated comparison uses the posted group-level counts to produce an unadjusted risk difference of -0.015, with a 95% confidence interval from -0.148 to 0.118 and p = 0.822.

These results differ in both effect measure and analysis approach. An odds ratio is not the same quantity as a risk difference, and a stratified analysis is not identical to a direct unadjusted comparison. The registry record does not identify the stratification factors, so the impact of stratification cannot be reconstructed from the posted information. The record flags no discrepancy between the recalculation and the reported analysis.

The sponsor’s analysis is the registry-reported inferential analysis, while the unadjusted recalculation offers a transparent comparison based on the group summaries. Neither result should be treated as a substitute for the other. Their intervals both reflect substantial uncertainty, and neither provides a clear separation between groups. The original statistical analysis plan is not reported in the registry record, so it is not possible to assess whether the sponsor’s reported method was the sole prespecified primary analysis or how it related to other planned analyses.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary endpoint and three secondary outcomes. It does not report a multiplicity adjustment or a testing hierarchy for these outcomes. When multiple hypotheses are tested, the chance of at least one apparently notable result can increase. In general, a prespecified strategy can control how results are interpreted across several outcomes, but no such strategy is described in the registry record. The secondary findings therefore warrant more caution than a single prespecified primary comparison.

The record identifies all randomized participants as the primary outcome population. It does not state how participants without an observed week-12 endpoint were handled, whether any imputation method was used, or how intercurrent events were treated. Missing-data choices can affect a response percentage, particularly if missing outcomes are more common in one group or related to the likelihood of response. No assumptions about those choices can be inferred from the posted results.

The registry record also does not report the original sample-size justification, the prespecified statistical analysis plan, or details of any interim analyses. It is therefore not possible to verify from this record whether the analysis methods, outcome hierarchy, or stopping decisions followed a prespecified plan. This is a limitation of the information available in the registry record, not evidence that a particular procedure was or was not used.

The primary outcome population is stated, but the registry does not provide enough detail to determine how it was implemented in practice or whether other analysis populations were used. Such information would help readers assess the robustness of the results. Without it, the interpretation should remain focused on the posted estimates and their uncertainty, while recognizing that analysis details relevant to missingness and multiplicity are not reported in the registry record.

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: colitis ulcerative (10.0%), pulmonary embolism (10.0%), covid-19 pneumonia (9.2%), congenital aural fistula (3.1%), enterocolitis infectious (3.1%).

The registry lists serious adverse event figures for three groups or treatment periods. For the Treatment group, 19 serious adverse events are reported among 87 participants at risk, and 2 deaths are listed. For Placebo, the figures are 2 among 10 at risk, with 0 deaths. For BMS-986165 6mg BID During OL Period After Receiving Placebo in Induction Period, the figures are 4 among 32 at risk, with 0 deaths. These are registry-reported counts and denominators; the record does not explain in this summary why the at-risk group sizes differ across these entries.

The listed serious adverse event terms include Colitis ulcerative and Pulmonary embolism, each reported as 10.0%, and COVID-19 pneumonia, reported as 9.2%. Other listed terms are Congenital aural fistula and Enterocolitis infectious, each 3.1%, and Anaemia, 1.1%. These entries describe reported events; they do not establish that a treatment caused an event. The record does not provide enough detail to interpret event timing, exposure duration, or attribution. Counts from groups with different denominators should not be compared without attention to those differences.

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

The primary result describes the proportion meeting a defined clinical remission endpoint at week 12 in the randomized treatment and placebo groups. The observed percentages were close, and the interval for the unadjusted between-group risk difference includes no difference and extends in both directions. The sponsor’s odds-ratio estimate and interval likewise leave substantial uncertainty. The posted results do not establish a clear treatment-placebo difference in clinical remission.

This is not the same as proving that the treatments are equivalent, or that no effect exists. A result with an interval spanning no difference can arise when the true effect is small, when estimates are imprecise, or through other features of the data and analysis. The registry record does not provide enough information to separate those possibilities. Equivalence would require a suitable prespecified design and margin, which are not reported in the registry record.

The findings are specific to this phase 2 trial, its enrolled participants, its endpoint definitions, and its reported assessment period. They do not establish what would happen with other doses, longer treatment, other patient groups, or different outcome definitions. The record identifies oral deucravacitinib as the intervention but does not provide randomized-arm dosing details in the posted information.

The secondary outcomes offer additional descriptions of clinical, endoscopic, and histological response, but their mixed directions and uncertainty do not resolve the primary comparison. The safety entries are counts and listed event terms, not proof of causation. Taken together, the registry record describes a trial with imprecise efficacy comparisons and safety events that require interpretation in the context of exposure, follow-up, and clinical assessment. It does not support medical advice or a conclusion about an individual participant’s care.

18. Why This Trial Matters Statistically

This trial illustrates why an observed percentage alone is not enough to judge a treatment comparison. The primary response rates are accompanied by confidence intervals, and the direct comparison has its own interval. The latter spans negative and positive risk differences, demonstrating that the estimate is compatible with more than one direction of effect. Looking at both the point estimate and its uncertainty gives a more complete statistical reading than focusing only on a p-value.

It also demonstrates that effect measures answer related but different questions. The recalculated risk difference expresses an absolute difference in response rates, while the sponsor’s stratified analysis reports an odds ratio. Their values cannot be compared on a common numerical scale. Understanding the method attached to each estimate is essential, particularly when a registry presents both a sponsor analysis and a simpler recalculation.

The trial is also a useful example of the limits of secondary outcomes. Several outcomes may add detail about different dimensions of response, but they bring additional comparisons and do not automatically strengthen the primary finding. Without a reported multiplicity plan, secondary results should be interpreted cautiously rather than treated as separate confirmatory evidence.

Finally, planning illustrations based on the observed effect can help show how uncertainty and target effect size relate to future study scale. They are not observed power and do not replace the original design rationale, which is not reported in the registry record. Separating the study’s reported findings from hypothetical planning calculations helps avoid confusing a completed trial’s results with a future-study design exercise.

19. Limitations

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

The registry record offers limited detail about several features that affect interpretation. The original sample-size justification and statistical analysis plan are not reported, as are the randomization procedures and the factors used in the sponsor’s stratified analysis. The record describes quadruple masking but does not identify the roles masked. These gaps prevent a detailed assessment of implementation and prespecification.

Although the primary outcome population is stated as all randomized participants, the registry record does not explain how missing week-12 assessments were handled. It also does not describe imputation, sensitivity analyses, or the treatment of participants who discontinued or otherwise did not complete assessment. The effect of these choices on the reported response rates cannot be evaluated from the available information.

The primary results come from a phase 2 study with 88 treatment participants and 43 placebo participants in the endpoint results. The confidence intervals indicate uncertainty in the group estimates and comparison. The record does not provide longer-term results among the outcomes, nor does it give detailed randomized-arm dosing information. Generalization beyond the studied population, intervention, and assessment period should therefore be cautious.

The secondary outcomes involve multiple comparisons, but no multiplicity approach is reported. The safety summary also includes entries with different at-risk group sizes and an open-label period after placebo induction; these entries are not directly interchangeable with the randomized comparison. The registry summary does not provide event timing, exposure duration, or attribution details needed to assess causal relationships. These limitations concern the detail available in the registry record and should not be interpreted as proof that the underlying study lacked additional procedures.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy of Deucravacitinib in Participants With Moderate to Severe Ulcerative Colitis — NCT03934216.
• Registry record last updated 2024-03-06; status last verified 2024-02.
• Results first posted 2022-07-06.
• 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

NCT03934216 is a completed phase 2 randomized, quadruple-masked, parallel-group, placebo-controlled study of deucravacitinib in participants with moderate to severe ulcerative colitis. Enrollment was 131. The primary endpoint was clinical remission response rate at week 12, with results reported for all randomized participants.

The reported remission percentages were 14.8% for treatment and 16.3% for placebo. The unadjusted risk-difference interval includes no difference, and the sponsor’s stratified odds-ratio analysis also reports a broad interval. The three secondary outcomes provide additional but mixed and uncertain comparisons. The registry record does not report the trial’s original sample-size justification, multiplicity strategy, or missing-data methods. Safety entries include serious adverse event counts and listed event terms, which should be interpreted descriptively rather than as evidence of causation.