A Study to Determine the Efficacy and Safety of Deucravacitinib Compared With Placebo in Participants With Active Psoriatic Arthritis (PsA) Who Are Naïve to Biologic Disease-modifying Anti-rheumatic Drugs: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Determine the Efficacy and Safety of Deucravacitinib Compared With Placebo in Participants With Active Psoriatic Arthritis (PsA) Who Are Naïve to Biologic Disease-modifying Anti-rheumatic Drugs (NCT04908202), a randomized phase 3 study. The primary outcome is Percentage of Participants With ACR 20 Response at Week 16.

2. Clinical Question

3. Trial Design

This is a Phase 3 randomized, double-blind, placebo-controlled study with a parallel-group design. The registry record classifies masking as quadruple. That label indicates a masking designation in the record, but the roles covered by it are not reported in the registry record. The study compares deucravacitinib with placebo in participants with active psoriatic arthritis who are naïve to biologic disease-modifying anti-rheumatic drugs.

The record lists enrollment of 670. In the posted primary outcome results, the randomized population comprises 336 participants assigned to deucravacitinib 6 mg once daily and 334 assigned to placebo. The primary assessment is at Week 16. The registry lists a start date of 2021-07-13, a primary completion date of 2024-10-10, and a status of active, not recruiting. These registry fields describe the study record; they do not establish that every study activity or follow-up period has ended.

The primary outcome is the percentage meeting ACR 20 response criteria. Secondary outcomes include joint disease activity, physical function, skin response, enthesitis, dactylitis, fatigue, and health-related quality of life. The record lists 59 outcome measures and 10 analyses, and 58 secondary outcomes have posted results. The available endpoint summaries include three secondary outcomes. The record also describes an intended long-term extension, but its additional efficacy and safety results are not presented in the Week 16 comparisons.

The registry record does not report the original sample-size justification, its planned effect size, or the detailed allocation procedures. It also does not report the full protocol-level statistical plan in the information available for this analysis. Those omissions mean that planning illustrations based on observed results should not be treated as evidence about how the trial was originally designed.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Pre-Treatment Period

Reasons for not completing this period:

Placebo-Controlled Treatment Period

Reasons for not completing this period:

Active Treatment Period

Reasons for not completing this period:

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

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 Percentage of Participants With ACR 20 Response at Week 16, measured over Week 16.

The primary endpoint is the percentage of participants with an ACR 20 response at Week 16. ACR 20 is a composite improvement criterion: a participant must have at least a 20% improvement from baseline in both tender and swollen joint counts, plus at least a 20% improvement in three of five additional core measures. Those measures cover participant assessments of pain and disease activity, a physician assessment of disease activity, physical function, and an acute phase reactant value. Baseline is defined as the last assessment before the first dose of single-blind study medication.

This type of endpoint is used to summarize improvement across several aspects of psoriatic arthritis rather than relying on a single symptom or measurement. The response threshold gives a clear classification for the reported percentage, while the underlying measures reflect different domains of disease activity and impact. A percentage response is readily compared between randomized groups, but it does not show the size or distribution of each participant’s change in every component. It also does not describe outcomes after Week 16.

The registry record reports a 95% confidence interval for each group’s response percentage, calculated using the Clopper-Pearson exact method. The endpoint therefore conveys both the observed response proportion and uncertainty around that proportion. It should be read as one prespecified primary outcome, not as a complete account of every possible benefit, harm, or longer-term outcome.

7. Results Posted in the Registry

• Placebo-Controlled Period - Placebo: 34.1% (114/334) versus 54.2% (182/336) on control; risk difference -20.0 percentage points (95% CI -27.4 to -12.7), risk ratio 0.63 (0.53–0.75); 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.

Change From Baseline in Disease Activity Score 28 C-reactive Protein (DAS28-CRP) at Week 16

• 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 deviations.
• Result:
  • Placebo-Controlled Period - Placebo: mean -0.89 versus -1.41 on control; difference 0.52 (95% CI 0.35 to 0.69), standardized effect d = 0.46; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Placebo-Controlled Period - Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Health Assessment Questionnaire - Disability Index (HAQ-DI) at Week 16

• 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 deviations.
• Result:
  • Placebo-Controlled Period - Placebo: mean -0.21 versus -0.41 on control; difference 0.20 (95% CI 0.12 to 0.28), standardized effect d = 0.38; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Placebo-Controlled Period - Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Meeting Psoriatic Area and Severity Index (PASI) 75 Response at Week 16, in Participants With at Least 3% Body Surface Area (BSA) Involvement and at Least Static Physician's Global Assessment (sPGA) 2 at Baseline

• 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:
  • Placebo-Controlled Period - Placebo: 7.1% (12/170) versus 51.9% (84/162) on control; risk difference -44.8 percentage points (95% CI -53.4 to -36.2), risk ratio 0.14 (0.08–0.24); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Placebo-Controlled Period - Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes span multiple domains: disease activity, physical function, skin involvement, enthesitis, dactylitis, fatigue, and health-related quality of life. The available detailed results include disease activity and physical function changes and a skin response in a defined baseline subgroup. For those selected outcomes, the posted group estimates and sponsor analyses are directionally consistent with the primary result, with results favoring the deucravacitinib group on the respective reported scales. This does not establish that every secondary outcome has the same pattern.

These outcomes complement the primary endpoint because they address different manifestations or consequences of psoriatic arthritis. They are not substitutes for ACR 20: some are continuous changes from baseline, some are percentages meeting a response criterion, and one is restricted to participants with specified skin involvement at baseline. The number of participants contributing to each endpoint can differ from the primary population, as can the outcome definition and analytic method. Comparisons across the outcomes should therefore remain endpoint-specific.

The record lists 59 outcome measures and 10 analyses, with 58 secondary outcomes posted. The registry information summarized for this analysis does not establish a complete multiplicity strategy, including whether particular secondary outcomes were adjusted for multiple testing, ordered in a testing hierarchy, or treated as descriptive. When many outcomes are examined, the chance of at least one apparently notable result can increase. Unadjusted secondary p-values consequently carry less confirmatory weight than a primary analysis specified for formal inference. The secondary findings are useful context, but they should be interpreted as a collection of distinct results rather than as multiple independent confirmations of the primary finding.

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

• Change From Baseline in Disease Activity Score 28 C-reactive Protein (DAS28-CRP) at Week 16
• Change From Baseline in Health Assessment Questionnaire - Disability Index (HAQ-DI) at Week 16
• Percentage of Participants Meeting Psoriatic Area and Severity Index (PASI) 75 Response at Week 16, in Participants With at Least 3% Body Surface Area (BSA) Involvement and at Least Static Physician's Global Assessment (sPGA) 2 at Baseline
• Change From Baseline in the 36-item Short Form (SF-36) Physical Subcomponent Summary (PCS) Score at Week 16
• Percentage of Participants Meeting Enthesitis Resolution (Score of 0) Among Participants With Enthesitis at Baseline by Leeds Enthesitis Index (LEI) at Week 16
• Percentage of Participants Meeting Achievement of Minimal Disease Activity (MDA) at Week 16
• Change From Baseline in Functional Assessment of Chronic Illness Therapy - Fatigue (FACIT-Fatigue) Score at Week 16
• Percentage of Participants Meeting Dactylitis Resolution at Week 16

9. Statistical Interpretation

10. Statistical Methods Explained

How should the response percentages be read?

The primary outcome is binary at the participant level: each participant either meets the ACR 20 response definition or does not. The group result is reported as a percentage, with a 95% confidence interval for each group. The confidence interval describes uncertainty in estimating the group’s response percentage from the participants included in that analysis. The registry specifies the Clopper-Pearson exact method for these intervals. This method is designed for proportions and is based on the binomial model; it is not an interval for an average change in a continuous score.

The posted primary denominators are 336 for deucravacitinib and 334 for placebo. The outcome description identifies the population as randomized. The record does not provide further details about how missing Week 16 assessments were handled or whether the analysis used additional imputation or sensitivity procedures. Those choices can affect the interpretation of a percentage endpoint, so their absence from the registry record limits what can be inferred about the analysis process.

What does the risk difference describe?

The unadjusted re-calculation compares the two observed response proportions by subtracting the deucravacitinib proportion from the placebo proportion. Consequently, a negative estimate corresponds to the placebo response percentage being lower. The posted estimate is -0.200, with a 95% confidence interval from -0.274 to -0.127. This is a simple comparison based on the posted summary counts, not the sponsor’s adjusted or stratified analysis. The unadjusted p-value is <0.001. A p-value describes how compatible the data are with a specified null hypothesis under the calculation’s assumptions; it does not state the probability that the null hypothesis is true.

General: a risk difference is expressed on the response-probability scale, making it a direct contrast between proportions. An odds ratio instead compares response odds, where odds are the response probability divided by the probability of no response. An odds ratio and a risk difference answer related but distinct questions. They need not have the same numerical scale or interpretation.

What is the sponsor’s analysis?

The sponsor reports a Cochran-Mantel-Haenszel analysis for the primary endpoint, with an odds ratio of 2.29, a 95% confidence interval from 1.67 to 3.13, and p < 0.001. This method estimates an association between treatment group and response while accounting for strata, if strata are specified in the analysis. The stratification factors and details of implementation are not reported in the registry record. The sponsor labels the result as a superiority analysis. Its odds ratio is therefore the posted sponsor analysis, while the simple risk difference is an unadjusted re-calculation from the posted summary statistics.

General: adjustment or stratification can produce a result that differs from a crude comparison because the analysis accounts for additional structure in the data. The registry record does not give enough detail to attribute any difference between the reported odds ratio and the simple risk difference to a particular adjustment factor. The sponsor’s own inferential analysis takes precedence as the trial’s reported analysis; the re-calculation is a descriptive check and not a replacement for the trial analysis.

How are the continuous secondary outcomes analyzed?

For the posted disease activity and physical function outcomes, the registry gives mean changes from baseline and standard deviations. The sponsor’s reported analyses use analysis of covariance (ANCOVA) and report adjusted mean differences, 95% confidence intervals, and p-values. ANCOVA is a regression-based method that compares groups while adjusting for variables included in the model. The covariates and model details are not reported in the registry record. The unadjusted comparisons use the posted means and pooled standard deviations to give a simple mean difference and its uncertainty. The sponsor’s adjusted result and the re-calculated unadjusted result are different estimands and should not be treated as interchangeable.

General: a mean difference is expressed in the original outcome scale, whereas a standardized effect expresses a difference relative to variability. These can help readers understand different aspects of an estimate, but neither alone establishes clinical importance. For continuous outcomes, the standard deviation describes spread among observations, not uncertainty in the mean itself. A confidence interval around the group contrast is needed to assess the precision of that contrast.

What assumptions matter for these methods?

General: methods for binary outcomes rely on an appropriate model for response counts and on a clear definition of the analysis population. Methods for continuous outcomes rely on suitable assumptions about the outcome distribution and model errors. Over-dispersion matters when observed variability in count or binary data is greater than a model allows; if present and unaccounted for, standard errors and confidence intervals may be too optimistic. The registry record does not report an over-dispersion assessment, and the posted primary analysis is described as Cochran-Mantel-Haenszel with an exact interval method for group percentages.

The registry provides selected endpoint definitions and sponsor analyses, but not the full statistical analysis plan, all model specifications, missing-data procedures, or sensitivity analyses. These omissions prevent a complete audit of assumptions and implementation from the registry record alone. The reported results can still be described as posted, but the distinction between reported analysis and simple re-calculation remains important.

11. Confidence Intervals and Precision

The primary group percentages have 95% confidence intervals: 48.7% to 59.6% for deucravacitinib and 29.1% to 39.5% for placebo. These intervals indicate that the observed response percentages are estimates rather than exact values for every possible participant in the study population. Their width reflects sampling uncertainty under the interval method and the available number of participants. They do not mean that 95% of individual participants’ responses lie within the interval.

For the unadjusted risk difference, the 95% confidence interval runs from -0.274 to -0.127. Because the contrast is calculated as placebo minus deucravacitinib, the entire interval is negative and the point estimate is negative. The sign must be read in conjunction with that calculation order. The sponsor’s odds-ratio interval, 1.67 to 3.13, is on a different scale and comes from the reported Cochran-Mantel-Haenszel analysis. Its values should not be directly compared numerically with the risk-difference interval.

Confidence intervals quantify precision for the specific parameter and method used. They do not account for every source of uncertainty, such as uncertainty arising from model choices, outcome selection, missing data, or departures from the analysis assumptions. The registry record does not report enough detail to evaluate all of those sources. Also, an interval that excludes a null value is not by itself a measure of clinical importance. Interpretation requires attention to the endpoint definition, effect scale, and the relevance of the observed difference.

The reported group intervals and contrast intervals answer related but different questions. A group interval estimates one group’s response percentage; a contrast interval estimates the difference between groups or the odds ratio. Overlap or non-overlap between separate group intervals is not a substitute for the sponsor’s direct comparison. The direct analysis and its own interval are the appropriate reference for inference on the stated treatment contrast.

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 illustrations translate selected effect assumptions into approximate sample sizes. For these non-time-to-event endpoints, the figures are participants per arm, not total participants across both arms. The assumptions listed for the illustrations are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each calculation uses the stated fraction of the observed effect as the effect to detect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column means the illustrated number of participants per arm under which the calculation would have an 80% chance of detecting the assumed effect at the specified significance level, if the assumptions and model hold. The 90% column describes the corresponding planning target with a higher chance of detecting that assumed effect. These are planning quantities, not guarantees that a future study will obtain a statistically significant result.

Rows that use 100%, 75%, and 50% of the observed effect illustrate how the estimate changes when the target effect is set smaller than the observed one. Smaller assumed effects require more participants per arm to reach the same target power. For example, the primary binary endpoint’s illustration gives 96 participants per arm for 80% power when using 100% of the observed effect, compared with 390 participants per arm when using 50% of the observed effect. These are illustrations derived from the observed result, not evidence about the trial’s original planning or operating characteristics.

The same logic applies to the associated curve: it shows how the planning estimate changes as the assumed detectable effect changes. It should be read as a conditional planning aid under the stated assumptions, rather than a forecast of results. This is not observed power; it does not measure the probability that the completed trial “had enough power” after its results were known. Time-to-event illustrations, when present, are reported as total numbers of events, but the outcomes discussed in these planning examples are not time-to-event outcomes.

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 = 0.542; treatment proportion p₁ = 0.341; average p̄ = 0.441.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7022 = 1.3764.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6878 = 0.5789.
4. n = (1.3764 + 0.5789)² / (-0.2003)² = 95.2, rounded up to 96 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 <- 0.541666666666667                          # control proportion
p1 <- 0.341317365269461                          # 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(4908202)
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 = 96 (80% power), 128 (90% power)
 75% of observed effect: n per arm = 172 (80% power), 230 (90% power)
 50% of observed effect: n per arm = 390 (80% power), 522 (90% power)
power.prop.test: 95.2 
Simulated power at n = 96 per arm: 0.801 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis is reported as a Cochran-Mantel-Haenszel odds ratio of 2.29, with a 95% confidence interval from 1.67 to 3.13 and p < 0.001. The registry labels this a superiority analysis. This is the trial’s reported inferential result and should take precedence over the simple re-calculation from group summary statistics.

The re-calculation compares the posted response percentages using an unadjusted risk difference, with placebo minus deucravacitinib as the subtraction order. It gives an estimate of -0.200, a 95% confidence interval from -0.274 to -0.127, and p <0.001. The negative sign reflects the ordering of the contrast. The re-calculation uses posted summary counts and does not reproduce the sponsor’s odds-ratio method or any stratification in that analysis.

The odds ratio and risk difference are different effect measures, so their numerical values cannot be compared directly. The registry record does not report the stratification factors or the detailed implementation of the sponsor’s analysis. The difference between the measures should therefore not be attributed to a particular model feature based on the information available. The two analyses are broadly consistent in the direction of the group contrast, but the sponsor’s analysis remains the designated reported analysis, while the unadjusted calculation is a transparent summary-statistic comparison.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is identified as the percentage of participants with ACR 20 response at Week 16, and the registry reports a sponsor analysis labeled as superiority. However, the registry record does not report a complete multiplicity plan for the primary and secondary outcomes. It does not state whether secondary tests were adjusted, arranged in a prespecified hierarchy, or intended mainly for descriptive interpretation. Without those details, the strength of confirmatory claims across the many posted outcomes cannot be fully assessed.

Multiplicity arises when researchers evaluate several outcomes, time points, or contrasts. General: if each test is judged separately at a conventional threshold, the chance of at least one false positive across a family of tests may be greater than the chance for one test alone. Adjustment procedures and prespecified testing sequences can address this issue, but they can also change how evidence is interpreted. The registry information does not identify such procedures for the results, so unadjusted secondary p-values should not be read as if they independently establish efficacy.

The primary outcome description identifies the randomized population and defines baseline as the last assessment before the first dose of single-blind study medication. The registry record does not report the full missing-data approach for the primary result, such as how participants without an observed Week 16 assessment were handled, or what sensitivity analyses were used. It also does not provide enough detail to determine whether the posted denominators include all randomized participants under a particular imputation or response rule. Missing outcome data can affect a response percentage if the probability of missingness is related to treatment or outcome.

The continuous secondary analyses are reported as ANCOVA, but model covariates and missing-data procedures are not reported in the registry record. Nor does the available information provide a complete account of analysis populations for each outcome beyond the primary outcome’s randomized population label. These details matter for judging whether the estimates answer an intention-to-treat question, how robust they are to missing observations, and whether sensitivity analyses support the main results. Their absence limits the assessment; it does not establish that the trial lacked such procedures.

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: prostate cancer (0.6%), angina unstable (0.3%), atrial fibrillation (0.3%), hiatus hernia (0.3%), cholelithiasis (0.3%).

The registry reports serious adverse events during both the placebo-controlled and active-treatment periods. During the placebo-controlled period, serious adverse events were reported for 6 of 332 at risk in the deucravacitinib group and 8 of 333 at risk in the placebo group. The record also reports 0 deaths in each of those groups. These counts describe the posted serious adverse event data for the stated period and at-risk denominators.

For the active-treatment period, the record lists 21 serious adverse events among 309 at risk in the deucravacitinib group and 17 among 306 at risk in the placebo-deucravacitinib group; deaths are reported as 0 in each group. The period labels differ, and the registry record does not provide enough detail to make these groups directly comparable as if they represented the same randomized contrast and follow-up conditions. The counts should therefore be read within their named treatment periods rather than combined or treated as a simple treatment effect.

Serious adverse event counts do not capture all adverse experiences, and they do not by themselves establish causation. The registry also lists serious event terms, but event-term percentages and counts are not a substitute for the overall serious-event totals. The available record does not provide a complete clinical assessment of event timing, relatedness, severity distribution, or exposure-adjusted rates. These figures describe what was posted, not a conclusion about overall safety.

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

The posted primary outcome shows that the Week 16 ACR 20 response percentage was higher in the deucravacitinib group than in the placebo group. The group estimates and confidence intervals describe the observed response proportions and their sampling precision. The sponsor’s reported odds-ratio analysis is consistent in direction with that contrast and is labeled as a superiority analysis. These are findings from the registry’s reported primary comparison, not proof that every participant responded or that every aspect of disease improved.

The primary endpoint is a composite threshold. Meeting ACR 20 means satisfying the specified improvement criteria across tender and swollen joint counts and additional core measures; it does not mean that all symptoms, domains, or quality-of-life measures improved by the same amount. Conversely, not meeting the threshold does not mean that a participant experienced no change. The group percentages summarize classifications, not the full range of individual responses.

The selected secondary results provide information on other outcomes, but they differ in scale, analysis, and population. They should not be merged into a single unqualified claim about all outcomes, particularly because the registry record does not report a full multiplicity plan. Likewise, the safety counts are descriptive and are not sufficient on their own to determine comparative risk or causality.

The results apply to the study population and assessment period described in the record: participants with active psoriatic arthritis who were naïve to biologic disease-modifying anti-rheumatic drugs, with primary assessment at Week 16. The record describes a long-term extension, but its results are not part of the comparisons. The registry record does not report enough information to establish how the Week 16 findings translate to other populations, longer follow-up, or individual treatment decisions. Statistical results describe group-level evidence; they do not provide medical advice.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through both its endpoint definition and its analysis scale. The primary endpoint is a percentage meeting a composite response threshold, while the sponsor’s formal comparison is expressed as an odds ratio. A simple re-calculation from posted summary statistics instead expresses the contrast as a risk difference. Keeping those measures distinct prevents readers from treating different effect scales as if they were interchangeable.

The record also illustrates the role of precision. Group percentages are accompanied by confidence intervals, and the direct contrast has its own interval. Those intervals communicate uncertainty more clearly than a p-value alone. The reported primary comparison and the unadjusted re-calculation point in the same direction, but the sponsor’s analysis remains the trial’s reported inferential result. Clearly separating reported analyses from summary-statistic re-calculations helps readers understand what was formally analyzed and what is a transparent descriptive check.

Finally, the range of secondary outcomes shows why multiplicity and missing-data methods matter. Different endpoints describe different facets of disease and can involve different populations and models. A consistent-looking pattern across selected measures can add context, but it does not remove the need to know how outcomes were prespecified, how missing observations were handled, and which analyses were confirmatory. Those details are not fully reported in the registry record. Recognizing what the posted results can answer—and what remains unresolved—is central to a careful statistical reading.

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 the original sample-size justification or its design assumptions. Planning illustrations based on the observed effect cannot fill that gap and should not be interpreted as evidence about the trial’s original design. The record also does not provide the full statistical analysis plan, the sponsor’s stratification factors for the primary Cochran-Mantel-Haenszel analysis, or the covariates used in the secondary ANCOVA models.

Missing-data handling and sensitivity analyses are not reported in sufficient detail in the record. This limits assessment of how unavailable Week 16 outcomes may have affected the response percentages and continuous outcome estimates. The record identifies the primary population as randomized, but the available information does not establish a full analysis-population definition for each secondary endpoint.

The trial lists many outcome measures, but a complete multiplicity strategy is not reported. This makes secondary p-values less suitable for confirmatory interpretation. Also, the detailed secondary results available for this analysis cover only selected outcomes; they should not be treated as a complete account of all posted secondary findings. The endpoints differ in scale and, for the skin response, are restricted to a specified baseline subgroup.

The safety figures are posted by treatment period and group, with differing at-risk denominators. The information does not provide sufficient detail about exposure duration, event relatedness, or the comparability of these periods to support a causal or exposure-adjusted comparison. Finally, the primary outcome is assessed at Week 16, and the registry’s long-term extension is described as a source of additional information; longer-term efficacy and safety results are not included in the comparisons.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Determine the Efficacy and Safety of Deucravacitinib Compared With Placebo in Participants With Active Psoriatic Arthritis (PsA) Who Are Naïve to Biologic Disease-modifying Anti-rheumatic Drugs — NCT04908202.
• Registry record last updated 2026-10-16; status last verified 2026-09.
• Results first posted 2025-10-24.
• 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

NCT04908202 is a Phase 3 randomized, parallel-group, double-blind, placebo-controlled study of deucravacitinib versus placebo in participants with active psoriatic arthritis who are naïve to biologic disease-modifying anti-rheumatic drugs. The registry classifies masking as quadruple and lists enrollment of 670. The primary outcome is the percentage of participants with ACR 20 response at Week 16.

The posted primary response percentages are 54.2% for deucravacitinib and 34.1% for placebo. The sponsor reports a Cochran-Mantel-Haenszel odds ratio of 2.29, with a 95% confidence interval from 1.67 to 3.13 and p < 0.001. The simple unadjusted re-calculation is a risk difference of -0.200, with a 95% confidence interval from -0.274 to -0.127.

The record lists secondary outcomes across several disease and health domains, alongside serious adverse event counts for distinct treatment periods. Full details on the original sample-size rationale, multiplicity strategy, and missing-data procedures are not reported in the registry record. The registry status is active, not recruiting, and the record lists a primary completion date of 2024-10-10.