A Study to Evaluate the Efficacy and Safety of Ruxolitinib Cream in Participants With Prurigo Nodularis (PN): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy and Safety of Ruxolitinib Cream in Participants With Prurigo Nodularis (PN) (NCT05764161), a randomized phase 3 study. The primary outcome is WI-NRS4 Response at Week 12.

2. Clinical Question

The primary endpoint is a responder outcome: each participant is classified according to whether their itch score improved by the specified threshold. The registry record describes the WI-NRS as a participant-reported rating of worst PN-related itch during the past 24 hours, on a scale from 0, “no itch,” to 10, “worst imaginable itch.” Baseline and post-baseline scores were based on averages of daily ratings, rather than one isolated daily score.

The trial also collected outcomes concerning itch response at other visits, overall-treatment success, an investigator assessment, changes in itch scores, and time to improvement. The primary comparison is specifically the randomized, double-blind, vehicle-controlled period. The registry record lists a later open-label extension for participants completing the double-blind period.

3. Trial Design

The registry record describes a Phase 3, randomized, quadruple-masked, parallel-group study with a vehicle control. It lists prurigo nodularis as the condition and Incyte Corporation as the sponsor. Enrollment was 190. The record gives a study start date of 2023-06-12, a primary completion date of 2024-12-30, and a status of completed.

During the double-blind, vehicle-controlled period, participants applied either ruxolitinib 1.5% cream or matching vehicle cream to affected areas twice daily for 12 weeks. The arm descriptions say that participants completing this period would enter an open-label extension for up to 40 weeks. The extension is distinct from the blinded vehicle comparison, so the primary endpoint is interpreted as a comparison during the initial controlled period, not as a comparison across the extension.

The primary endpoint was the percentage achieving a WI-NRS reduction of at least 4 points from baseline at Week 12. The outcome description says the primary analysis used the Intent-to-Treat population, defined as all randomized participants, with groups determined by randomized assignment regardless of the study cream actually applied during the double-blind period. It also states that participants missing Week 12 data for any reason were classified as nonresponders.

The primary outcome lists 94 participants in the vehicle group and 95 in the ruxolitinib group. These outcome denominators are reported alongside the endpoint results; they should not be treated as a reconstruction of every participant’s trial experience. The registry record does not report the original design’s sample-size justification or the assumptions used to choose its enrollment target.

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: Participants were enrolled at 52 sites in Australia, Austria, Bulgaria, Canada, France, Germany, Italy, South Korea, Poland, Spain, Switzerland, and the United States.

12-week DBVC Period

Reasons for not completing this period:

40-week OLE Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat (ITT) Population: all randomized participants. Treatment groups were defined according to the treatment assignment at the time of randomization regardless of the actual study cream the participant might have applied during their participation in the double-blind, vehicle-controlled period. Participants with a baseline ITCH Score ≥4 were analyzed.

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 WI-NRS4 Response at Week 12, measured over Baseline; Week 12.

The primary endpoint is the percentage of participants with a WI-NRS response at Week 12. A response means at least a 4-point reduction from baseline in the Worst-Itch Numeric Rating Scale. The WI-NRS is a participant-reported single-item measure of worst PN-related itch during the previous 24 hours, scored from 0, “no itch,” to 10, “worst imaginable itch.”

To reduce reliance on a single day’s rating, the record defines baseline as the average of the 7 daily scores before Day 1 and each post-baseline visit score as the average of the 7 daily scores before that visit. Participants without Week 12 data, including those who discontinued treatment for any reason, were counted as nonresponders. Thus, the endpoint combines observed improvement with a specific missing-data rule.

A threshold-based response outcome can make results easier to interpret as the proportion reaching a prespecified degree of improvement. It also compresses information: participants just below the threshold and participants with little change are both classified as nonresponders, while the size of improvement among responders is not represented by the response percentage alone. That is a general feature of binary responder endpoints, not an additional finding from this study.

The endpoint addresses the proportion meeting the specified itch-improvement criterion at the stated visit. It does not, by itself, describe every aspect of itch, the course of symptoms at every visit, or the balance of benefits and harms.

7. Results Posted in the Registry

• Ruxolitinib 1.5% Cream BID to Ruxolitinib 1.5% Cream BID: 40.0% (38/95) versus 36.2% (34/94) on control; risk difference 3.8 percentage points (95% CI -10.0 to 17.7), risk ratio 1.11 (0.77–1.59); unadjusted two-proportion z-test p = 0.588.

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.

WI-NRS4 Response at Week 4

• 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:
  • Ruxolitinib 1.5% Cream BID: 30.5% (29/95) versus 19.1% (18/94) on control; risk difference 11.4 percentage points (95% CI -0.8 to 23.6), risk ratio 1.59 (0.95–2.67); unadjusted two-proportion z-test p = 0.070.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ruxolitinib 1.5% Cream BID and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Overall-Treatment Success 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:
  • Ruxolitinib 1.5% Cream BID: 12.5% (12/96) versus 6.4% (6/94) on control; risk difference 6.1 percentage points (95% CI -2.1 to 14.4), risk ratio 1.96 (0.77–5.00); unadjusted two-proportion z-test p = 0.150.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ruxolitinib 1.5% Cream BID and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With IGA-CPG-S-TS 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:
  • Ruxolitinib 1.5% Cream BID: 24.0% (23/96) versus 10.6% (10/94) on control; risk difference 13.3 percentage points (95% CI 2.7 to 23.9), risk ratio 2.25 (1.13–4.47); unadjusted two-proportion z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Ruxolitinib 1.5% Cream BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes covering itch response at Week 4, Day 7, and other post-baseline visits; change in WI-NRS scores; overall-treatment success; IGA-CPG-S-TS; and time to a WI-NRS improvement. These measures examine related but distinct aspects of outcome, including response at different times, score change, and investigator-assessed or overall success. The record lists 27 posted secondary outcomes.

Across the three secondary outcomes with detailed results in the registry record, the point estimates are directionally higher in the ruxolitinib group than in the vehicle group. The amount of statistical uncertainty differs across those comparisons. The secondary results therefore provide context around the primary endpoint, but they do not resolve the uncertainty in the Week 12 primary response comparison. A secondary measure may capture a different construct or visit and should not be treated as interchangeable with the primary WI-NRS4 endpoint.

Secondary analyses are often interpreted with less weight when many outcomes or time points are examined. As a general statistical matter, looking across many tests increases the chance that some results appear notable by chance, even if no underlying differences exist. The registry record does not report whether or how the secondary analyses were adjusted for multiplicity, so the posted secondary p-values should be read as unadjusted unless otherwise specified in the registry results.

The record does not report a prespecified hierarchy for these secondary outcomes or a multiplicity-control strategy. It is therefore not possible to establish from the registry record which secondary findings, if any, were intended as confirmatory. Their role is descriptive and supportive in interpreting the broader set of measured outcomes, rather than a substitute for the primary result.

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

• WI-NRS4 Response at Week 4
• Percentage of Participants With Overall-Treatment Success at Week 12
• Percentage of Participants With IGA-CPG-S-TS at Week 12
• WI-NRS4 Response at Day 7
• WI-NRS4 Response at Each Post-baseline Visit
• DBVC Period: Change From Baseline in WI-NRS Score at Each Post-baseline Visit
• OLE Period: Change From Baseline in WI-NRS Score at Each Post-baseline Visit
• Time to ≥2-point Improvement From Baseline in WI-NRS Score

9. Statistical Interpretation

10. Statistical Methods Explained

What is being compared?

The primary outcome is binary at the participant level: a participant either met the WI-NRS4 response criterion at Week 12 or did not. A response required at least a 4-point improvement from baseline. The registry reports the percentage of participants responding in each randomized group. The primary population is described as the Intent-to-Treat population, with participants analyzed according to assignment at randomization, regardless of the cream actually applied during the double-blind period.

For a binary outcome, a risk difference compares the response proportions by subtracting one group’s proportion from the other. It expresses the absolute separation between the groups on the response scale. The registry’s primary reported response-rate difference is 3.81, with a 95% confidence interval from -9.84 to 17.46. The posted recalculation gives an unadjusted risk difference of 0.038, with a 95% confidence interval from -0.1 to 0.177. The reported difference and the recalculated difference arise from different posted summaries and analysis approaches; the sponsor’s analysis is the registry’s own reported analysis.

What does an odds ratio describe?

An odds ratio compares the odds of response between groups. Odds are not the same as probabilities, so an odds ratio is not a direct measure of the difference in response percentages. An odds ratio of 1 corresponds to equal odds; values above or below 1 indicate the direction of the estimated comparison according to the ordering of groups. The sponsor reports a Cochran-Mantel-Haenszel odds ratio of 1.18. The registry record does not specify the adjustment factors used in that analysis, so no particular stratification or covariate adjustment should be inferred from the method label alone.

The posted recalculation uses the group summary counts and is described as an unadjusted re-calculation. It gives an odds ratio of 1.176 and an unadjusted p-value of 0.588. The sponsor’s reported odds ratio is 1.18 with p = 0.586. The numerical closeness of these results does not make the methods identical; one is the registry’s own reported analysis and the other is an unadjusted calculation from the posted summaries.

How should a confidence interval be read?

A confidence interval describes the range of effect values compatible with the data and the interval method under its assumptions. It is not a range in which the individual participant outcomes fall, nor does it assign a probability that the true effect is within the particular interval. A narrow interval indicates greater precision than a broad interval, all else equal. For this primary comparison, both the reported response-rate difference interval and the recalculated interval include no difference. This is consistent with substantial uncertainty about the magnitude and direction of the group separation.

What does a p-value contribute?

A p-value describes how unusual the observed data, or data more extreme, would be under a specified null hypothesis and the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The sponsor reports p = 0.586 for the primary odds-ratio analysis; the unadjusted recalculation gives p = 0.588. Neither number should be read as proof of no effect. The registry record does not report a complete primary statistical analysis plan or a prespecified decision threshold, so further details about how the primary test was intended to guide decisions are not reported in the registry record.

Why use a responder definition?

Turning a continuous score into a response indicator gives a proportion that can be understood as the share reaching a stated improvement threshold. The trade-off, as a general statistical matter, is loss of detail: the response variable does not retain the exact change in score, and participants with different degrees of nonresponse are grouped together. The registry lists change from baseline in WI-NRS scores among secondary outcomes, which addresses a different aspect of the data than the primary responder endpoint.

Because the endpoint is binary, its uncertainty depends on both response rates and the number of participants contributing to the comparison. The reported confidence intervals communicate that uncertainty. They should be considered along with the missing-data rule, which classifies missing Week 12 results as nonresponses. The registry record does not report sensitivity analyses exploring alternative assumptions for missing primary data.

11. Confidence Intervals and Precision

The primary response estimates have 95% confidence intervals. The vehicle group’s response was 36.2%, with a 95% confidence interval from 26.5% to 46.7%. The ruxolitinib group’s response was 40.0%, with a 95% confidence interval from 30.1% to 50.6%. The intervals overlap substantially, and the reported response-rate difference interval runs from -9.84 to 17.46. The recalculated risk-difference interval also includes no difference.

These intervals show that the observed percentages do not precisely pin down the size of the group separation. The point estimate favors a higher response percentage in the ruxolitinib group, but plausible values represented by the interval include a lower response percentage as well as a higher one relative to vehicle. The interval therefore does not support treating the point estimate as a precise estimate of the effect.

Confidence intervals are useful because they display both an estimate and its uncertainty. In general, a confidence interval is constructed by a method that, under repeated use and its assumptions, has a stated coverage property. It does not mean that a particular interval has a 95% probability of containing the true effect. Its interpretation also depends on the analysis method and the data assumptions.

The posted outcome counts and percentages are limited to the registry’s specified analysis and missing-data rule. The registry record does not report sensitivity analyses for the primary endpoint that would show how precision or estimates change under alternative missing-data assumptions. The confidence intervals quantify sampling uncertainty under the analysis used; they do not account for every possible source of uncertainty, such as limitations in outcome measurement or applicability to other settings.

For the primary comparison, the sponsor’s odds-ratio interval is 0.651 to 2.143. It includes 1, the odds-ratio value corresponding to no difference. The sponsor’s response-rate difference interval also includes no difference. This broad uncertainty is important context: the observed estimates alone do not settle how large, if any, the underlying group difference is.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculations. For these binary-outcome illustrations, the figures are participants per arm, not total participants or total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect.

The 80% power column gives the illustrated number of participants per arm for a design that would have an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding planning number for a 90% chance. These are design calculations for hypothetical future studies, not a measure of what the completed trial achieved.

Rows that plan for a smaller fraction of the observed effect require more participants per arm than rows based on the full observed effect. This reflects a general statistical relationship: smaller differences are harder to distinguish from sampling variation, so more information is needed to detect them with the same planned power. The illustration uses the observed effect as its starting point, which is uncertain and may not be a stable estimate of an effect in another study.

These values are not observed power. The trial’s own original sample-size assumptions and justification are not reported in the registry record. The time-to-event planning tables, if applicable, are described in the record as giving total events; the binary-outcome planning figures discussed for this comparison are participants per arm. These planning numbers do not change the interpretation of the completed trial’s outcome estimates or confidence intervals.

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 = 0.362; treatment proportion p₁ = 0.400; average p̄ = 0.381.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6867 = 1.3460.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6862 = 0.5775.
4. n = (1.3460 + 0.5775)² / (0.0383)² = 2,522.5, rounded up to 2,523 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 <- 0.361702127659574                          # control proportion
p1 <- 0.4                          # 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(5764161)
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 = 2,523 (80% power), 3,377 (90% power)
 75% of observed effect: n per arm = 4,464 (80% power), 5,975 (90% power)
 50% of observed effect: n per arm = 9,993 (80% power), 13,377 (90% power)
power.prop.test: 2522.5 
Simulated power at n = 2,523 per arm: 0.802 (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’s primary reported analysis is a Cochran-Mantel-Haenszel odds ratio of 1.18, with a 95% confidence interval from 0.651 to 2.143 and p = 0.586. It also reports a response-rate difference of 3.81, with a 95% confidence interval from -9.84 to 17.46. The odds-ratio interval includes 1, while the difference interval includes no difference.

The recalculation from posted summary statistics is unadjusted. It gives an odds ratio of 1.176, with a 95% confidence interval from 0.654 to 2.118 and an unadjusted p-value of 0.588. Its risk-difference estimate is 0.038, with a 95% confidence interval from -0.1 to 0.177. The recalculated values are close to, but not identical to, the registry’s own results. The record does not report enough detail to attribute the small numerical differences to a specific analysis feature.

The discrepancy flag is false. Accordingly, the sponsor’s reported analysis remains the primary reference for the sponsor’s own inferential result; the recalculation is a transparent, unadjusted comparison derived from the posted summary statistics, not a replacement for that analysis. Both approaches convey uncertainty that includes no group difference. Neither should be interpreted as proving equivalence or as establishing the absence of an effect.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint analysis uses the Intent-to-Treat population, described in the registry record as all randomized participants and grouped according to randomized assignment. The endpoint description states that participants with missing Week 12 data for any reason, including treatment discontinuation, were defined as nonresponders. This rule is important because missing outcomes are not simply omitted from the response definition; they are assigned a specific outcome classification.

That approach provides a clear rule for the primary response calculation, but the result depends in part on that rule. The registry record does not report sensitivity analyses using alternative assumptions about missing data, nor does it report detailed reasons for missing Week 12 assessments by group. The record’s stated rule therefore does not show how the estimated group comparison might change under other plausible missing-data assumptions.

The posted primary outcome lists 94 participants in the vehicle group and 95 in the ruxolitinib group. Some secondary outcomes list different denominators, including 96 in the ruxolitinib group for Week 12 secondary measures. The registry record does not provide enough information in the registry record to explain every denominator variation, so its cause is not reported in the registry record. Each outcome’s own denominator should be used when reading its estimate.

Multiplicity concerns arise because the registry reports many secondary outcomes across different measures and visits. In general, testing many hypotheses without adjustment raises the chance of at least one apparently unusual result under a setting where there is no true difference for all the outcomes. The registry record does not report whether the secondary tests were adjusted, whether a testing sequence was prespecified, or whether interim analyses were conducted. Those details are not reported in the registry record and should not be inferred from the number of outcomes alone.

The registry record also does not report the complete statistical analysis plan, a prespecified clinical-importance threshold, or the trial’s original sample-size justification. These gaps limit conclusions about the intended confirmatory testing framework beyond the endpoint definitions and analyses explicitly listed.

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: erysipelas (1.1%), intervertebral disc protrusion (1.1%), angina unstable (0.6%), breast cancer (0.6%), chronic obstructive pulmonary disease (0.6%).

The registry reports serious adverse events for the vehicle group among 94 participants at risk, with 0 affected, and for the ruxolitinib group among 178 participants at risk, with 9 affected. It reports other adverse events for 4 of 94 participants at risk in the vehicle group and 29 of 178 in the ruxolitinib group. The registry also lists 0 deaths in the vehicle group and 1 in the ruxolitinib group.

These are the event figures and denominators reported in the adverse-event record. They should be read separately from the primary endpoint population counts; the adverse-event denominator for the ruxolitinib group is 178, while the primary outcome lists 95. The registry entries do not explain the denominator difference, so its reason is not reported in the registry record.

Event counts alone do not establish that an event was caused by the study cream. The registry record does not provide a causal attribution for the listed events or the death. Serious-event terms listed include erysipelas and intervertebral disc protrusion at 1.1% each, and angina unstable, breast cancer, chronic obstructive pulmonary disease, and completed suicide at 0.6% each. These figures describe reported events, not comparative causal conclusions.

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

The primary result is an observed Week 12 WI-NRS4 response of 40.0% in the ruxolitinib group and 36.2% in the vehicle group. The registry-reported response-rate difference is 3.81, with a 95% confidence interval from -9.84 to 17.46. The sponsor’s odds-ratio analysis has a 95% confidence interval that includes 1 and p = 0.586. Together, these results show that the observed estimates are uncertain and do not clearly distinguish the groups statistically.

This does not establish that the treatments are equivalent, and it does not prove that there is no difference. A nonsignificant result can occur when the true difference is small, when estimates are imprecise, or for other reasons. The confidence interval is more informative than a binary significant/not-significant label because it shows a range of values compatible with the data under the analysis assumptions.

Nor does the result, by itself, establish a clinically important improvement or lack of improvement. The registry record does not report a clinical-importance threshold for the primary endpoint. It also does not describe every participant’s score trajectory, since the primary result reduces score changes to whether a response threshold was reached, with missing Week 12 data classified as nonresponse.

The findings are specific to the measured endpoint, visit, population, and randomized vehicle-controlled period. They do not alone determine results for other populations, durations, outcomes, or the open-label extension. Secondary outcomes add context, but their interpretation is limited by multiple comparisons and the absence of a reported multiplicity approach. Safety event counts should likewise be read as reported events rather than as proof of causation.

Overall, the registry results show a modest observed difference in response percentages with intervals broad enough to include no difference. The posted information supports describing the estimate and its uncertainty; it does not justify a definitive claim that ruxolitinib cream works or does not work.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate should be read together with its uncertainty. The response percentages are not identical, but the primary confidence intervals encompass no difference and cover a broad range of possible group separations. Focusing only on which group has the higher percentage would miss the imprecision that is central to the statistical interpretation.

It also demonstrates the interpretive effect of a responder definition. The primary endpoint translates a patient-reported itch scale into a proportion achieving at least a 4-point reduction. That can make the target outcome concrete, while concealing the range of score changes within the responder and nonresponder categories. The registry’s secondary change-from-baseline outcomes reflect a different way to describe the same broad symptom domain.

The missing-data rule matters because a participant without a Week 12 assessment is classified as a nonresponder. This makes the endpoint definition explicit, but leaves unanswered how results might differ under alternative assumptions. The primary outcome denominators and adverse-event denominators also differ in the registry record, reinforcing the need to keep each analysis population and outcome denominator distinct.

Finally, the record contains multiple secondary outcomes and reports no multiplicity strategy. This illustrates why secondary findings should be interpreted as a family of exploratory or supportive evidence unless a confirmatory testing plan is documented. Planning illustrations based on observed effects can help readers understand the scale of future-study requirements, but they are not the original trial’s design justification or a measure of its observed power.

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 primary outcome is based on a dichotomized WI-NRS change, so it does not preserve the full magnitude of each participant’s score change. Its interpretation also depends on the threshold of at least a 4-point reduction and the classification of missing Week 12 data as nonresponse. The registry record does not report sensitivity analyses for alternative missing-data assumptions.

The primary comparison has broad confidence intervals that include no difference. This limits precision about the size and direction of the underlying difference. The sponsor’s reported analysis and the unadjusted recalculation are close but not identical; the recalculation cannot reproduce any analysis details not contained in the posted summary statistics. The registry record does not report the adjustment factors for the Cochran-Mantel-Haenszel analysis.

The registry lists many secondary outcomes, but does not report a multiplicity adjustment, testing hierarchy, or full statistical analysis plan. Secondary findings should therefore be interpreted cautiously. The original design’s sample-size justification and assumptions are also not reported in the registry record, so the observed enrollment cannot be evaluated against a stated design target from these registry entries.

Some outcome denominators vary across the posted results, and the adverse-event denominator for the ruxolitinib group differs from the primary endpoint denominator. The registry record does not explain these differences in the registry record. The serious adverse-event and death counts also do not specify causal attribution. Finally, the randomized comparison concerns the 12-week controlled period; outcomes during the open-label extension are not equivalent to a continued blinded comparison against vehicle.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy and Safety of Ruxolitinib Cream in Participants With Prurigo Nodularis (PN) — NCT05764161.
• Registry record last updated 2026-11-06; status last verified 2026-10.
• Results first posted 2025-11-24.
• 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

The registry record describes a completed Phase 3, randomized, quadruple-masked, parallel-group study of ruxolitinib 1.5% cream versus matching vehicle cream in participants with prurigo nodularis. The double-blind, vehicle-controlled treatment period lasted 12 weeks, with an open-label extension listed for up to 40 weeks.

The primary endpoint was the percentage achieving at least a 4-point reduction in WI-NRS score at Week 12. The reported response rates were 40.0% with ruxolitinib and 36.2% with vehicle. The sponsor-reported response-rate difference was 3.81, with a 95% confidence interval from -9.84 to 17.46; the sponsor-reported odds ratio was 1.18, with p = 0.586.

The primary comparison is uncertain, and its confidence interval includes no difference. Missing Week 12 outcomes were classified as nonresponses. The registry lists multiple secondary outcomes and adverse-event counts, but does not report a multiplicity strategy, the original sample-size justification, or a complete statistical analysis plan.