Etrasimod Versus Placebo for the Treatment of Moderately to Severely Active Ulcerative Colitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Etrasimod Versus Placebo for the Treatment of Moderately to Severely Active Ulcerative Colitis (NCT03945188), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving Clinical Remission at Week 12.

2. Clinical Question

The primary endpoint is a binary outcome: each participant either met the registry’s clinical-remission definition at Week 12 or did not. The registry defines remission using the modified Mayo score (MMS), which combines participant-reported symptoms from a daily eDiary with centrally read endoscopy. Its components are stool frequency, rectal bleeding, and endoscopic score.

The registry reports clinical remission in 27.0% of the etrasimod 2 mg group and 7.4% of the placebo group. The posted comparison is a risk difference, so its focus is the absolute separation in the percentage achieving the outcome, rather than a relative measure. The registry also reports a Cochran-Mantel-Haenszel analysis classified as superiority.

This is a question about a defined endpoint in a specified population and at a specified time. It does not, by itself, answer broader questions about every possible clinical outcome, every participant with ulcerative colitis, or outcomes beyond those reported in the record.

3. Trial Design

The registry describes a Phase 3, randomized, double-blind, placebo-controlled, parallel study of etrasimod in participants with moderately to severely active ulcerative colitis. The official title specifies a 52-Week study. The record lists 433 enrolled participants and identifies Arena Pharmaceuticals as the sponsor. The study is marked completed.

Participants were assigned to etrasimod 2 mg or placebo. For the primary endpoint, the posted arm sizes are 274 for etrasimod 2 mg and 135 for placebo. The primary analysis population is the FAS, defined in the record as all randomized participants who received at least 1 dose of study treatment and had actual Baseline MMS 5 to 9. The safety figures use different at-risk counts, which are described separately in the safety discussion; the reason for the difference is not reported in the registry record.

The primary outcome was assessed at Week 12. The record also lists outcomes assessed at Week 12 and Week 52, including endoscopic improvement, symptomatic remission, and mucosal healing, as well as outcomes at Week 52 involving corticosteroid-free clinical remission and sustained clinical remission at both Weeks 12 and 52. The registry lists 23 outcome measures and 61 analyses.

The record gives a start date of 2019-06-13 and a primary completion date of 2022-02-08. Specific details such as the method used to generate the randomization sequence, allocation concealment, masking procedures, adherence, and the trial’s original sample-size justification are not reported in the registry record. The existence of a randomized, double-blind design does not establish the details of those procedures.

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: The study included a Screening Period (up to 28 days), a 12-Week Treatment Period (induction) followed by a 40-Week Treatment Period (maintenance; for which no re-randomization took place), and a 2-Week and 4-Week Follow-Up Period.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS (consisting of all randomized participants who received at least 1 dose of study treatment) with actual Baseline MMS 5 to 9.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Full Analysis Set (FAS): All randomized participants who received at least 1 dose of study treatment.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving Clinical Remission at Week 12, measured over At Week 12.

The primary endpoint is the percentage of participants achieving clinical remission at Week 12. The registry defines remission through the modified Mayo score (MMS), a composite of stool frequency, rectal bleeding, and endoscopic score. Stool frequency and rectal bleeding are participant-reported using a daily eDiary; endoscopy is centrally read.

Remission requires a stool-frequency subscore of 0, or 1 with at least a 1-point decrease from baseline; a rectal-bleeding subscore of 0; and an endoscopic score of 1 or less, excluding friability. Each component subscore ranges from 0 to 3, while the total MMS ranges from 0 to 9; higher scores indicate more severe disease. These rules make the endpoint a prespecified combination of symptoms and endoscopic findings rather than a single symptom or examination result.

A binary endpoint is used to report the proportion meeting the definition, allowing the two groups to be compared in terms of how often remission was recorded at the specified assessment. This type of endpoint is understandable, but it compresses the underlying measurements: participants who narrowly miss the full definition and those with more severe symptoms both count as not achieving remission. The registry’s primary population further restricts the endpoint to participants with actual Baseline MMS 5 to 9 who received at least 1 dose after randomization.

The endpoint describes the outcome at Week 12. It does not alone characterize the course of symptoms between assessments or establish the meaning of outcomes beyond the registry’s definition.

7. Results Posted in the Registry

• Etrasimod 2 mg: 27.0% (74/274) versus 7.4% (10/135) on control; risk difference 19.6 percentage points (95% CI 12.7 to 26.5), risk ratio 3.65 (1.95–6.83); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants Achieving Endoscopic Improvement 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:
  • Etrasimod 2 mg: 35.0% (96/274) versus 14.1% (19/135) on control; risk difference 21.0 percentage points (95% CI 12.8 to 29.1), risk ratio 2.49 (1.59–3.89); 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 Etrasimod 2 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Achieving Endoscopic Improvement at Week 52

• 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:
  • Etrasimod 2 mg: 37.2% (102/274) versus 10.4% (14/135) on control; risk difference 26.9 percentage points (95% CI 19.2 to 34.6), risk ratio 3.59 (2.14–6.03); 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 Etrasimod 2 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Achieving Symptomatic Remission 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:
  • Etrasimod 2 mg: 46.0% (126/274) versus 21.5% (29/135) on control; risk difference 24.5 percentage points (95% CI 15.4 to 33.6), risk ratio 2.14 (1.51–3.03); 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 Etrasimod 2 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The listed secondary outcomes cover several related aspects of ulcerative colitis, including endoscopic improvement, symptomatic remission, mucosal healing, corticosteroid-free clinical remission, and sustained clinical remission. Some are assessed at Week 12, others at Week 52, and the sustained-remission outcome requires remission at both stated assessments. The registry lists 21 posted secondary outcomes, while the brief outcome list also identifies outcomes at both assessment times and combined time points.

The posted secondary results for the outcomes with arm-level summaries show higher percentages in the etrasimod group than the placebo group. This broad direction is consistent with the primary Week 12 clinical-remission comparison. The endpoints are not interchangeable, however: symptom-based outcomes, endoscopic outcomes, and outcomes requiring persistence across assessments capture different aspects of the disease and use different definitions. Their estimates should be interpreted according to each endpoint’s stated assessment time and criteria.

The registry’s primary result is the designated primary endpoint comparison. Secondary analyses add context about other outcomes but do not automatically have the same inferential status. The registry lists 23 outcome measures and 61 analyses; the procedure for controlling multiplicity or prioritizing hypotheses is not reported in the registry record. In general, when many outcomes are tested, unadjusted p-values can overstate the strength of evidence across the whole set because the chance of at least one apparently significant finding can increase.

Accordingly, secondary findings are best read as supportive descriptive evidence unless the analysis plan and multiplicity strategy establish a stronger confirmatory role. Their direction can be considered alongside the primary result, but not as independent proof that every outcome differs reliably. The registry record does not provide the complete analysis plan, missing-data procedures, or enough detail to assess all secondary comparisons in their intended testing sequence.

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

• Percentage of Participants Achieving Endoscopic Improvement at Week 12
• Percentage of Participants Achieving Endoscopic Improvement at Week 52
• Percentage of Participants Achieving Symptomatic Remission at Week 12
• Percentage of Participants Achieving Symptomatic Remission at Week 52
• Percentage of Participants With Mucosal Healing at Week 12
• Percentage of Participants With Mucosal Healing at Week 52
• Percentage of Participants Achieving Corticosteroid-free Clinical Remission at Week 52
• Percentage of Participants Achieving Sustained Clinical Remission at Both Weeks 12 and 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: participants either achieved the registry’s clinical-remission definition at Week 12 or did not. The arm percentages describe the observed proportion meeting that definition. A comparison of those proportions can be expressed as a risk difference, which is the absolute difference between the event proportions. In general, an absolute measure is useful because it keeps the contrast tied to the observed outcome frequency. It does not describe relative change, and it should not be confused with an odds ratio or risk ratio.

What does the risk difference represent?

For this endpoint, the recalculated estimate is 0.196, with a 95% confidence interval from 0.127 to 0.265. This is the simple unadjusted re-calculation from the posted summary statistics. The sponsor reports a risk difference of 19.75 with a 95% confidence interval from 12.88 to 26.63, using a Cochran-Mantel-Haenszel analysis. The record identifies the sponsor result as a superiority analysis and reports p < 0.001. The record does not flag a discrepancy between the sponsor result and the recalculation.

In general, the Cochran-Mantel-Haenszel method can estimate an association or treatment contrast while accounting for stratification. The strata or other details relevant to the sponsor’s implementation are not reported in the registry record, so the method cannot be reconstructed fully from this information. The re-calculation does not incorporate any such adjustment. It is useful as a straightforward check of the posted arm summaries, but it is not a replacement for the sponsor’s stated analysis.

What does a confidence interval add?

In general, a confidence interval gives a range of estimates compatible with the data under the statistical method and its assumptions. It communicates precision as well as direction. A narrower interval indicates greater statistical precision than a wider interval on the same scale, while an interval that spans the no-difference value leaves more uncertainty about the direction of the contrast. The primary re-calculated interval is entirely positive, as is the sponsor’s reported interval. Neither interval accounts for every source of uncertainty, such as possible bias in measurement or limitations in how participants were selected.

A p-value and a confidence interval are related summaries, but they answer different questions. In general, the p-value evaluates how surprising data at least as extreme as those observed would be under a specified null hypothesis and model. It is not the probability that the null hypothesis is true, and it does not measure the probability that the findings will replicate. The confidence interval presents a range for the effect estimate and makes its uncertainty easier to inspect. Here, the registry reports p < 0.001 for both the recalculation and sponsor analysis.

What does the endpoint definition contribute?

The MMS combines stool frequency, rectal bleeding, and endoscopic score. The remission rule requires all stated component criteria to be satisfied, so the outcome reflects a composite threshold rather than a change in just one component. In general, composite endpoints can capture more than one clinically relevant domain, but interpretation depends on the exact components and thresholds. A binary composite also discards detail about how close a participant came to the threshold or which component was not met.

The primary population is described as the FAS, consisting of randomized participants who received at least 1 dose and had actual Baseline MMS 5 to 9. This definition is narrower than a simple statement that all randomized participants were analyzed. The record does not report how missing Week 12 assessments were handled, whether any additional analysis populations were used for the sponsor’s primary inference, or how the baseline restriction was implemented in the statistical model.

Why distinguish the reported and recalculated analyses?

Statistical results can differ when methods make different adjustments, even when they address the same endpoint and comparison. An unadjusted calculation works directly from the posted event summaries. A stratified analysis can incorporate design or analysis strata, depending on the method’s implementation. In general, adjusted and unadjusted estimates need not be identical. Since the registry record reports a sponsor Cochran-Mantel-Haenszel analysis, that result is the appropriate description of the trial’s own stated analysis; the recalculation is an additional, simple comparison and should be interpreted as such.

Multiplicity is another methodological issue when a study has several outcomes or analyses. In general, testing many hypotheses can increase the chance of at least one small p-value if the testing strategy does not account for the number and ordering of tests. The record lists 23 outcome measures and 61 analyses, but does not report a multiplicity procedure or a hierarchy that would show how confirmatory claims were controlled. Therefore, the primary result can be described as reported, while the evidential status of secondary findings requires additional caution.

Finally, a statistically detectable difference is not by itself a full assessment of clinical importance. Statistical significance concerns compatibility with a statistical null model; clinical importance depends on the endpoint, the size and precision of the contrast, the broader evidence, and context not fully captured in the registry entry. The observed endpoint percentages and confidence intervals describe the primary Week 12 comparison, but they do not answer every question about benefits, harms, durability, or generalizability.

11. Confidence Intervals and Precision

The recalculated primary risk difference is 0.196, with a 95% confidence interval from 0.127 to 0.265. The sponsor’s Cochran-Mantel-Haenszel result is a risk difference of 19.75, with a 95% confidence interval from 12.88 to 26.63. Both intervals lie on the positive side of no difference, consistent with the reported p < 0.001 for each analysis. The estimates use different formats and methods, so the interval values should be read within their respective analyses rather than treated as identical calculations.

In general, a confidence interval represents the uncertainty around an estimate under the method used. It is not a range containing a fixed proportion of individual participant outcomes, nor does a 95% interval mean there is a 95% probability that this particular interval contains the true effect. The confidence level describes the long-run behavior of the interval procedure under its assumptions.

The interval width conveys statistical precision, but precision is not the same as absence of bias. A confidence interval can be relatively informative while still not accounting for problems such as missing outcome data, measurement limitations, or limitations in the analysis population. The registry record does not provide enough detail to evaluate all those issues. It also does not report the trial’s original sample-size justification or other design assumptions needed to assess precision against the planned target.

The endpoint is a percentage-based binary outcome, and the comparison is an absolute risk difference. Its estimate is tied to the Week 12 assessment and the stated FAS population. The reported interval should not be generalized to the Week 52 outcomes, other populations, or different definitions of remission. For secondary outcomes, the corresponding uncertainty and multiplicity context also matter when interpreting the broader set of findings.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning illustration concerns participants per arm, not total events. Its assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for planning is a stated fraction of the observed effect. The registry’s original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative participants per arm under the stated assumptions for a design with an 80% chance of detecting the chosen effect if that effect were the true one. The 90% power column gives the corresponding planning figure for a design with a 90% chance under those same assumptions. These are design calculations, not evidence about the probability that the trial’s finding is true or will replicate.

The rows consider planning for 100%, 75%, and 50% of the observed effect. Smaller effects need more participants to detect with the same power under otherwise unchanged assumptions. The resulting numbers are illustrations based on the observed effect and the stated statistical setup, rather than a reconstruction of the trial’s intended enrollment plan.

This is not observed power. Observed power calculated from the estimated effect after a trial is complete does not provide a useful substitute for examining the estimated effect and its confidence interval. The registry reports an enrollment of 433, but the planning illustration should not be read as the rationale for that enrollment or as proof that the trial was adequately powered for every endpoint. The original design assumptions are not reported in the registry record.

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 = 0.074; treatment proportion p₁ = 0.270; average p̄ = 0.172.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5338 = 1.0462.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5155 = 0.4338.
4. n = (1.0462 + 0.4338)² / (0.1960)² = 57.0, rounded up to 58 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 <- 0.0740740740740741                          # control proportion
p1 <- 0.27007299270073                          # 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(3945188)
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 = 58 (80% power), 76 (90% power)
 75% of observed effect: n per arm = 91 (80% power), 121 (90% power)
 50% of observed effect: n per arm = 176 (80% power), 235 (90% power)
power.prop.test: 57 
Simulated power at n = 58 per arm: 0.832 (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 sponsor’s own primary analysis is a Cochran-Mantel-Haenszel risk-difference analysis. It reports a risk difference of 19.75, a 95% confidence interval from 12.88 to 26.63, and p < 0.001. The registry classifies this as a superiority analysis. The recalculation is a simple unadjusted comparison from the posted arm summaries, with a risk difference of 0.196, a 95% confidence interval from 0.127 to 0.265, and p < 0.001.

These are not identical procedures: the sponsor analysis uses the stated Cochran-Mantel-Haenszel method, whereas the recalculation is unadjusted. Both point in the same direction and report a positive risk difference. The record does not flag a discrepancy, but the sponsor result is the trial’s reported analysis and should be distinguished from the supplemental recalculation. The registry does not describe the strata or other implementation details needed to reproduce the sponsor analysis fully.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 23 outcome measures and 61 analyses, indicating that the record contains multiple endpoints and comparisons. The primary endpoint is clearly identified as clinical remission at Week 12. However, a complete statistical plan specifying which hypotheses were confirmatory, the order in which they were tested, or whether a family-wise error or other multiplicity procedure was used is not reported in the registry record.

In general, multiplicity matters because testing many outcomes can increase the probability of obtaining at least one small p-value by chance when all null hypotheses are true. Prespecified testing hierarchies or adjustment procedures can address this issue, but the applicable approach cannot be inferred from the number of registry entries alone. The record’s classification of the primary sponsor result as superiority does not reveal how the broader set of hypotheses was managed.

Missing-data handling is also not reported in the registry record. The FAS definition states that participants were randomized, received at least 1 dose, and had actual Baseline MMS 5 to 9, but it does not explain how missing Week 12 endpoint measurements were treated, whether participants with incomplete assessments were counted as non-remitters, or whether imputation or sensitivity analyses were used. These details can affect a binary endpoint estimate, so their absence limits assessment of robustness.

The original statistical analysis plan, interim-analysis procedures, and sample-size justification are not reported in the registry record. These omissions do not erase the stated endpoint results, but they constrain evaluation of whether the analysis followed its intended protocol, how much inferential weight should be assigned to secondary outcomes, and how the sample size was selected. No particular procedure should be assumed where the record does not state one.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: colitis ulcerative (2.1%), large intestine perforation (0.7%), covid-19 pneumonia (0.7%), covid-19 (0.7%), campylobacter infection (0.7%).

The safety record reports serious adverse events among 20 participants at risk in the etrasimod 2 mg group and 9 participants at risk in the placebo group; the respective at-risk counts are 289 and 144. The record reports 0 deaths in each group. These safety denominators differ from the primary endpoint arm sizes, which are based on the stated FAS population. The reason for the difference is not reported in the registry record, so the safety counts should be interpreted using their own at-risk denominators rather than substituted for the efficacy population.

The most frequently listed serious adverse-event terms include colitis ulcerative at 2.1%, and large intestine perforation, COVID-19 pneumonia, COVID-19, Campylobacter infection, and cellulitis at 0.7% each. These terms describe events recorded as serious adverse events; they do not establish that the study treatment caused them. The record also reports other adverse events in 204 participants at risk in the etrasimod group and 77 participants at risk in the placebo group.

Safety figures require caution: events can differ in severity, duration, relatedness, and clinical context, and the registry summary does not give individual-level details or a full causal assessment. The listed counts and terms are descriptive registry results, not a complete comparison of all potential harms.

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

The registry reports that a larger percentage of participants in the etrasimod 2 mg group achieved the defined clinical-remission outcome at Week 12 than in the placebo group. The reported sponsor analysis and the unadjusted recalculation both estimate a positive difference, with p < 0.001 and confidence intervals that do not include no difference. This supports a statistical distinction between the groups for this endpoint under the reported analyses.

That result does not establish that every participant benefits, nor does it describe an individual’s likely outcome. The endpoint is a composite binary measure, and a participant either met all required criteria or did not. It does not convey the degree of change in each component for participants who did not meet the full definition. Nor does a Week 12 result by itself describe outcomes throughout the 52-Week study or beyond it.

The result also does not resolve the full balance of efficacy and safety. Serious adverse-event counts and selected terms are recorded, but the registry summary does not provide enough detail to attribute events to treatment or to characterize every safety dimension. It does not report the complete statistical analysis plan, missing-data methods, or multiplicity strategy. These gaps limit how fully the posted outcome estimates can be evaluated.

In general, statistical significance is not synonymous with clinical importance. The absolute percentages, estimated contrast, and confidence intervals describe the observed result and its statistical precision; judging its importance requires clinical context and consideration of the broader evidence. The trial’s population is also specific: the primary analysis used participants who received at least 1 dose and had actual Baseline MMS 5 to 9. Results should not automatically be extended to people outside that defined population or to outcomes that were not reported.

The finding is therefore best read as evidence of a group difference for the stated Week 12 endpoint in the stated analysis population, accompanied by uncertainty and limitations in the registry entries. It is not a complete account of long-term effects, all outcomes, individual experience, or the totality of evidence.

18. Why This Trial Matters Statistically

This trial is statistically informative because it pairs a clearly defined binary primary endpoint with a randomized, double-blind, placebo-controlled, parallel design. Randomization and masking are important design features in general because they can reduce some sources of systematic group differences and assessment bias. The registry identifies those features, although detailed procedures for implementing them are not reported.

The outcome combines participant-reported symptoms and centrally read endoscopy. That makes the endpoint broader than a single symptom measure, while also making the precise remission threshold important to interpretation. The risk difference is a direct absolute contrast between the percentages achieving the outcome, and the confidence interval communicates uncertainty around that contrast.

The posted primary results include both the sponsor’s Cochran-Mantel-Haenszel analysis and an unadjusted recalculation based on the arm summaries. Their positive direction provides a useful consistency check across the stated analysis and the simple recalculation, while the distinction between methods remains important. The registry also includes several secondary outcomes across symptom, endoscopic, and longer-term measures, which makes multiplicity and analysis-plan transparency relevant to the strength of broader claims.

Finally, the record illustrates why efficacy, precision, population definition, and safety denominators should be read together. The primary endpoint population and safety at-risk counts are not the same, and the registry does not explain the difference. Clear reporting of these analysis populations, missing-data handling, and multiplicity procedures would help readers assess the robustness and scope of the findings. The available results still permit a focused interpretation of the Week 12 primary endpoint, without assuming details not stated in the record.

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 does not report several details needed to fully evaluate the trial’s conduct and analysis. These include the randomization sequence method, allocation concealment, masking procedures, adherence, the original sample-size justification, and the complete statistical analysis plan. The record also does not state whether interim analyses were performed or how multiplicity was controlled across outcomes and analyses.

Missing-data methods for the primary and secondary outcomes are not reported. This matters because the primary endpoint is binary and depends on measured symptom and endoscopic components at Week 12. Without the handling rules for incomplete assessments, the robustness of the reported percentages cannot be fully assessed. The registry defines the primary population as FAS participants who received at least 1 dose and had actual Baseline MMS 5 to 9, but does not give a fuller account of analysis-population decisions.

The primary endpoint is limited to a specific composite definition and time point. It does not capture every aspect of disease experience, and a participant who narrowly misses one criterion is counted differently from one who misses several. The reported secondary outcomes broaden the picture but are subject to uncertainty about the multiplicity strategy and analysis hierarchy.

The efficacy arm sizes and safety at-risk counts differ, and the reason is not reported in the registry record. The safety summary offers serious adverse-event totals, selected terms, other adverse-event counts, and deaths, but not enough detail to establish causality or describe the complete safety profile. Finally, this is a registry record for a defined trial population; generalizability beyond the eligibility and endpoint population cannot be determined from these summaries alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Etrasimod Versus Placebo for the Treatment of Moderately to Severely Active Ulcerative Colitis — NCT03945188.
• Registry record last updated 2022-12-20; status last verified 2022-03.
• Results first posted 2022-12-20.
• 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

NCT03945188 is a completed Phase 3 randomized, double-blind, parallel study comparing etrasimod 2 mg with placebo in moderately to severely active ulcerative colitis. The official title describes a 52-Week study. The registry lists Arena Pharmaceuticals as sponsor, enrollment of 433, a start date of 2019-06-13, and a primary completion date of 2022-02-08.

The primary endpoint was the percentage achieving clinical remission at Week 12, based on the modified Mayo score. The posted percentages were 27.0% for etrasimod 2 mg and 7.4% for placebo. The sponsor reports a Cochran-Mantel-Haenszel risk difference of 19.75, with a 95% confidence interval from 12.88 to 26.63 and p < 0.001. The unadjusted recalculation is positive as well.

The record includes secondary outcomes and safety information, but does not report the full analysis plan, multiplicity procedures, or missing-data methods. Those omissions limit assessment of broader claims beyond the stated primary comparison.