Topical Ruxolitinib Evaluation in Chronic Hand Eczema: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Topical Ruxolitinib Evaluation in Chronic Hand Eczema (NCT05906628), a randomized phase 2 study. The primary outcome is Percentage of Participants With Investigator's Global Assessment-Chronic Hand Eczema Treatment Success (IGA-CHE-TS) at Week 16.

2. Clinical Question

3. Trial Design

NCT05906628 is a completed phase 2 randomized, triple-masked, parallel-group trial of topical ruxolitinib for chronic hand eczema. The registry lists an enrollment of 186 and identifies Incyte Corporation as the sponsor. The study start date is 2023-07-31, and the primary completion date is 2024-07-15. The registry describes the initial treatment period as a 16-week, double-blind, vehicle-controlled comparison, followed by an open-label extension.

The two assigned groups were ruxolitinib cream 1.5% twice daily and vehicle cream twice daily. During the first 16 weeks, the randomized groups provide the direct comparison relevant to the primary endpoint. During the additional 16-week extension, participants initially assigned to ruxolitinib continued that treatment, while participants initially assigned to vehicle crossed over to ruxolitinib. Once both groups receive ruxolitinib, their extension-period outcomes do not represent a continuing randomized comparison of ruxolitinib against vehicle.

The primary analysis was defined for the Intent-to-Treat population, consisting of all randomized participants analyzed according to their assignment at randomization, regardless of the treatment they actually applied. The record identifies the primary outcome as the percentage achieving IGA-CHE treatment success at Week 16. It also lists itch, pain, and IGA-CHE outcomes among the secondary measures. The registry record does not report the trial’s original sample-size justification, the detailed statistical analysis plan, or whether interim analyses were planned.

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: This study was conducted at 30 study centers in Canada, Germany, Poland, and the United States.

16-Week DBVC Period

Reasons for not completing this period:

16-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 participants who were randomized to the study. Treatment groups were defined according to the treatment assignment at the time of randomization regardless of the actual study treatment the participant might have applied during their participation in the study. Missing post-Baseline values were imputed as nonresponders.

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 Investigator's Global Assessment-Chronic Hand Eczema Treatment Success (IGA-CHE-TS) at Week 16, measured over Baseline; Week 16.

The primary endpoint is the percentage of participants with Investigator’s Global Assessment-Chronic Hand Eczema treatment success at Week 16. IGA-CHE rates global chronic hand eczema severity on a five-point scale from 0, clear, to 4, severe. The listed descriptions also identify 1 as almost clear, 2 as mild eczema, and 3 as moderate eczema.

Treatment success is a combined threshold: a participant must have an IGA-CHE score of 0 or 1 at Week 16 and must have improved by at least 2 steps from baseline. Thus, the outcome captures both the state reached at follow-up and the degree of change from the participant’s starting assessment. It is not simply a measure of average score change, nor does it count every improvement as success.

A binary success outcome can be clinically interpretable because it describes the proportion of participants who cross a prespecified response threshold. At the same time, reducing a graded measure to success or non-success discards information about changes that do not meet the threshold and about differences among participants within either category. The registry record does not report additional validation details or the rationale for choosing this threshold beyond the endpoint definition.

7. Results Posted in the Registry

• Ruxolitinib 1.5% Cream BID to Ruxolitinib 1.5% Cream BID: 53.2% (50/94) versus 10.9% (10/92) on control; risk difference 42.3 percentage points (95% CI 30.4 to 54.2), risk ratio 4.89 (2.65–9.05); 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.

Number of Participants With Any ≥Grade 3 TEAE in the DBVC Period

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • DBVC Period: Vehicle Cream BID: 1.1% (1/92) versus 2.1% (2/94) on control; risk difference -1.0 percentage points (95% CI -4.6 to 2.6), risk ratio 0.51 (0.05–5.54); unadjusted two-proportion z-test p = 0.573.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DBVC Period: Vehicle Cream BID and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Any TEAE in the OLE Period

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Open-label Extension (OLE) Period: Ruxolitinib 1.5% Cream BID: 11.9% (10/84) versus 32.5% (25/77) on control; risk difference -20.6 percentage points (95% CI -33.1 to -8.0), risk ratio 0.37 (0.19–0.71); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Open-label Extension (OLE) Period: Ruxolitinib 1.5% Cream BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Any ≥Grade 3 TEAE in the OLE Period

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Open-label Extension (OLE) Period: Ruxolitinib 1.5% Cream BID: 1.2% (1/84) versus 1.3% (1/77) on control; risk difference -0.1 percentage points (95% CI -3.5 to 3.3), risk ratio 0.92 (0.06–14.40); unadjusted two-proportion z-test p = 0.951.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Open-label Extension (OLE) Period: Ruxolitinib 1.5% Cream BID and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering itch response, itch-score change, time to itch improvement, IGA-CHE treatment success over post-baseline visits, pain-score change, and pain response or time to pain improvement. These outcomes broaden the questions beyond the primary Week 16 success threshold, including symptom measures and the timing of improvement. Numerical findings for those listed secondary efficacy outcomes are not reported in the registry record.

The available numerical secondary results concern treatment-emergent adverse events during the controlled and open-label extension periods. Those safety outcomes address a different domain from IGA-CHE success and cannot be used as confirmation or contradiction of the primary efficacy result. Nor should the open-label extension be read as a randomized efficacy comparison: participants initially assigned to vehicle crossed over to ruxolitinib.

Secondary outcomes can help describe whether findings extend across related measures, but their interpretation depends on how many outcomes were tested, whether analyses were prespecified, and whether adjustment for multiple comparisons was planned. The registry record does not report a multiplicity strategy for these outcomes. When many outcomes are examined without adjustment, the chance of at least one apparently notable result arising by chance can increase. For that reason, secondary results without a stated multiplicity plan generally carry less confirmatory weight than a clearly designated primary endpoint. The absence of posted numerical efficacy findings also prevents a meaningful assessment of whether the secondary symptom measures align with the primary outcome.

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

• Percentage of Participants Achieving ITCH4 Response at Weeks 4 and 16
• Percentage of Participants Achieving ITCH4 Response at Day 3 and Week 1 (Day 7)
• Percentage of Participants With Investigator's Global Assessment-Chronic Hand Eczema Treatment Success (IGA-CHE-TS) at Each Post-Baseline Visit
• Change From Baseline in CHE-related Itch NRS Score at Each Post-Baseline Visit
• Time to ≥4-point Improvement From Baseline in CHE-related Itch NRS Score
• Change From Baseline in CHE-related Pain NRS Score at Each Post-Baseline Visit
• Percentage of Participants Achieving ≥2-point Improvement in CHE-related Skin Pain NRS Score From Baseline to Week 16
• Time to ≥2-point Improvement From Baseline in CHE-related Skin Pain NRS Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the IGA-CHE treatment-success definition at Week 16 or did not. For a binary endpoint, a group response percentage estimates the share of participants classified as responders. Comparing those shares can be expressed in several ways, including a risk difference or an odds ratio. Each measure answers a related but distinct question, so the estimate and its scale should be stated clearly.

What does a risk difference express?

A risk difference subtracts one group’s response probability from the other group’s response probability. The recalculated result is 0.423, with a 95% confidence interval from 0.304 to 0.542. In percentage-point terms, the sponsor reports a response-rate difference of 42.5, with a 95% confidence interval from 30.70 to 54.36. The registry’s response-rate difference and the simple recalculation are close but are not identical; the reported analysis may use a different method or precision than an unadjusted calculation. The registry record does not give further detail for the response-rate difference analysis.

What does an odds ratio express?

An odds ratio compares the odds of success in one group with the odds in the other. The sponsor reports an odds ratio of 9.82, with a 95% confidence interval from 4.48 to 21.49, using a Cochran-Mantel-Haenszel method. This method can combine comparisons across strata when stratification is part of the analysis. The registry record does not identify the strata or provide further details about how they were used. An odds ratio is not a response percentage, and it should not be read as a direct multiple of the probability of success.

Why are there multiple estimates?

The sponsor’s reported odds ratio and response-rate difference are distinct summaries of the randomized comparison. The recalculated risk difference is an unadjusted calculation from the group summary statistics. Differences between estimates can arise because methods target different quantities or handle the data differently. The registry record does not report enough detail to reconstruct every aspect of the sponsor’s calculations. The posted sponsor analysis is therefore best treated as the reported trial analysis, while the unadjusted result provides a transparent descriptive comparison based on the displayed group summaries.

What do the p-values say?

The sponsor reports p < 0.001 for the odds-ratio analysis, and the unadjusted recalculation reports p < 0.001. A p-value is calculated under a statistical model that assumes a null value for the comparison. It indicates how unusual data at least as inconsistent with that null would be if the model and null hypothesis were correct. It does not give the probability that the null is true, measure the probability that the result will repeat, or describe the size of an effect. Interpretation should place the estimate and its confidence interval alongside the p-value.

Why does the analysis population matter?

The primary endpoint description identifies the Intent-to-Treat population as all participants randomized, assigned to groups according to randomization regardless of the treatment they might actually have applied. This preserves the randomized grouping for the primary comparison. It also means the estimate is about outcomes by original assignment, rather than an effect restricted to participants who adhered to treatment. The registry record does not report further details about handling missing Week 16 assessments, protocol deviations, or other analysis-population definitions.

Why can over-dispersion matter in general?

In general, over-dispersion occurs when observed variation is greater than a statistical model expects. If it is ignored, standard errors and confidence intervals can be too small, making results appear more precise than they are. This is a general statistical consideration for models of event counts or proportions, not a reported feature of this trial’s analysis. The registry record does not report an over-dispersion assessment or a model adjustment for it.

What does masking contribute?

The registry classifies the trial as triple-masked and randomized. In general, masking can reduce the influence of expectations on treatment delivery, participant reporting, and outcome assessment, depending on who is masked and how the procedure is implemented. The record does not state which three roles were masked or give implementation details. The endpoint includes an investigator assessment, making the integrity of assessment procedures relevant, but the registry description alone does not establish how masking was maintained.

11. Confidence Intervals and Precision

The primary group estimates are accompanied by 95% confidence intervals: 42.6% to 63.6% for the ruxolitinib group and 5.3% to 19.1% for the vehicle group. A confidence interval gives a range of values compatible with the data under the statistical method used. In repeated use of the same method under its assumptions, intervals at this confidence level would cover the target quantity at the stated rate. It is not a guarantee that a particular interval contains the true value.

The sponsor’s reported odds ratio is 9.82, with a 95% confidence interval from 4.48 to 21.49. The unadjusted risk difference is 0.423, with a 95% confidence interval from 0.304 to 0.542; the sponsor’s response-rate difference is 42.5, with a 95% confidence interval from 30.70 to 54.36. These intervals quantify sampling uncertainty for their respective measures. They should not be compared as if they were intervals on the same scale.

Precision depends partly on the number of participants and events and on the statistical method. The primary group sizes were 94 and 92. The observed intervals give a sense of the remaining uncertainty despite the clear separation in the estimates. A narrow interval would indicate greater precision on its own scale; a wider interval would leave a broader range of plausible values. The registry record does not report an adjusted confidence interval for the risk difference beyond the sponsor’s reported response-rate result.

Confidence intervals do not capture every source of uncertainty. They do not resolve questions about endpoint choice, missing-data handling, generalizability, or the effects of unreported analysis decisions. They also do not establish that every participant would experience an outcome resembling the group average. Interpretation should consider the endpoint definition, analysis population, and trial design as well as the numerical width of the intervals.

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 illustrations describe hypothetical planning for a future two-arm comparison, using the observed effect as a starting point. The assumptions listed are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculations consider detecting the stated fraction of the observed effect. The original trial’s own sample-size justification and design assumptions are not reported in the registry record.

For binary outcomes, the planning figures are participants per arm. The 80% power column gives the number of participants per arm estimated to provide an 80% chance of detecting the assumed effect if that effect is real and the planning assumptions hold. The 90% power column uses a higher target chance of detection, which generally requires more participants. These are planning illustrations, not observed power.

Each row changes the effect assumed for planning: 100%, 75%, or 50% of the observed effect. Smaller assumed effects require more participants because a smaller separation between groups is harder to distinguish from random variation. The figures should not be read as a recommendation for a future study without considering its endpoint, population, analysis, feasibility, and chosen effect of interest. The calculations use a simplified normal approximation and equal allocation; the registry record does not report that these assumptions were the original trial’s design assumptions.

For time-to-event outcomes, the stated convention is total events rather than participants per arm. The primary endpoint is a percentage of participants with an event, so its planning figures follow the participants-per-arm convention. The listed figures are conditional on the observed effect and the specified assumptions, and they do not show the probability that the trial result is true.

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 = 0.109; treatment proportion p₁ = 0.532; average p̄ = 0.320.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6599 = 1.2933.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5881 = 0.4950.
4. n = (1.2933 + 0.4950)² / (0.4232)² = 17.9, rounded up to 18 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 <- 0.108695652173913                          # control proportion
p1 <- 0.531914893617021                          # 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(5906628)
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 = 18 (80% power), 24 (90% power)
 75% of observed effect: n per arm = 30 (80% power), 39 (90% power)
 50% of observed effect: n per arm = 58 (80% power), 77 (90% power)
power.prop.test: 17.9 
Simulated power at n = 18 per arm: 0.823 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison using the Cochran-Mantel-Haenszel method for an odds ratio of 9.82, with a 95% confidence interval from 4.48 to 21.49 and p < 0.001. It also reports a response-rate difference of 42.5, with a 95% confidence interval from 30.70 to 54.36. These are the trial’s reported analyses.

The accompanying recalculation is an unadjusted comparison derived from the posted group summaries. It gives a risk difference of 0.423, with a 95% confidence interval from 0.304 to 0.542 and p < 0.001. It is a simple summary calculation rather than a reconstruction of every part of the sponsor’s analysis. The registry marks no discrepancy between the posted and recalculated results. The two presentations are consistent in direction and broadly similar in the size of the response contrast, while using different reported methods and formats.

The recalculation is useful as a transparent check of the group-level result, but it does not replace the sponsor’s method or establish what covariates, strata, or other details were used beyond those reported. Where a sponsor analysis is reported, it should be identified as such rather than silently substituted with a simpler calculation. The registry record does not provide further specifications for the response-rate difference analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome: IGA-CHE treatment success at Week 16. It also lists multiple secondary measures, including repeated assessments over visits and itch- and pain-related outcomes. Testing multiple outcomes can increase the chance of a false-positive finding if each is interpreted using an unadjusted threshold. A multiplicity plan may control that risk through a prespecified testing sequence or another adjustment, but such a plan is not reported in the registry record.

The record does not report whether secondary comparisons were adjusted for multiplicity, which secondary outcomes were confirmatory, or whether any hierarchy governed their testing. Consequently, secondary p-values, if available elsewhere, should not automatically be interpreted with the same confirmatory force as the primary analysis. Numerical efficacy results for the listed secondary endpoints are not reported in the registry record.

The primary endpoint description specifies an Intent-to-Treat population comprising all randomized participants, analyzed according to randomization assignment irrespective of treatment actually applied. That definition is relevant because it preserves the original randomized groups. However, the registry record does not report the extent or handling of missing Week 16 endpoint data, the imputation method if any, sensitivity analyses for missingness, or how participants without an assessable outcome were classified.

Missing outcome data can affect interpretation when the likelihood of an assessment being unavailable is related to treatment or outcome. Different assumptions about missing participants can lead to different estimates. The record also does not provide a detailed statistical analysis plan, the specific handling of protocol deviations, or a full account of analysis populations beyond the stated primary ITT definition. These omissions limit the ability to independently assess robustness, even though the randomized design and reported primary analysis remain interpretable at the level described.

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: retinal artery embolism (1.1%), brain neoplasm (0.6%), cardiac arrest (0.6%), osteoarthritis (0.6%), prostatic obstruction (0.6%).

The registry reports serious adverse events in the vehicle group for 1 of 92 participants at risk and in the ruxolitinib group for 5 of 171 participants at risk. It reports zero deaths in the vehicle group and 1 death in the ruxolitinib group. The listed groups and denominators are the registry’s safety summary; the ruxolitinib safety denominator includes more participants than the initial randomized group, so it should not be compared as if both figures represented the same exposure period and population.

The registry lists serious-event terms including retinal artery embolism at 1.1%, and brain neoplasm, cardiac arrest, osteoarthritis, prostatic obstruction, and sinus node dysfunction at 0.6% each. These are event listings, not evidence that treatment caused the events. Serious adverse events are a safety category and should be distinguished from any treatment-emergent adverse event; the record’s event counts do not establish causation.

Counts are uncommon and do not by themselves provide a precise estimate of comparative safety. The registry record does not report adjudication details or a causal assessment for these events. Safety interpretation should account for the different denominators and the treatment crossover during the extension, and should not infer that an event was caused by treatment merely because it occurred during the study.

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

The primary result describes the proportion of randomized participants who met a specific IGA-CHE success definition at Week 16. In this trial, the reported percentage was 53.2% for participants assigned to ruxolitinib and 10.9% for participants assigned to vehicle. The sponsor’s analysis and the unadjusted recalculation both indicate a marked difference in the observed response proportions, with uncertainty expressed by their respective confidence intervals.

This result does not mean that every participant assigned to ruxolitinib achieved success, or that no participant assigned to vehicle did. The outcome is a threshold-based classification; it does not describe all degrees of improvement, symptom burden, or individual experience. It also does not determine whether the size of the observed contrast is important to every patient or clinician. The registry record does not report a minimum clinically important difference for this endpoint.

The primary comparison concerns the double-blind, vehicle-controlled period through Week 16. The extension is open-label and includes crossover from vehicle to ruxolitinib, so it cannot maintain the same randomized treatment contrast. The posted information also does not provide numerical results for the listed secondary efficacy outcomes, limiting conclusions about consistency across itch, pain, and other measures.

The trial was conducted in adults with chronic hand eczema and moderate to severe disease activity as described in the registry. Its results should not automatically be generalized to people with different disease severity, other populations, or different treatment schedules. The record does not establish longer-term outcomes beyond the reported study periods, comparative effectiveness against treatments other than vehicle, or the cause of individual adverse events.

Statistical evidence about a group comparison is not an individualized prediction. The estimates summarize outcomes under the trial design and analysis, while uncertainty, selection criteria, endpoint construction, missing-data handling, and unreported analysis details all matter when considering what the result can support.

18. Why This Trial Matters Statistically

This trial illustrates how a binary clinical endpoint can turn a graded investigator assessment into a response proportion that is straightforward to describe. The IGA-CHE success definition requires both a low Week 16 severity score and a change from baseline. Reporting the threshold and the group percentages makes clear what the response means, rather than leaving the endpoint as an unexplained label.

It also demonstrates why an estimate should be read with its uncertainty. The group response percentages and their confidence intervals describe the observed trial results, while the risk difference and odds ratio express the comparison on different scales. A p-value alone would not convey either the size of the contrast or the range of values compatible with the data.

The study’s randomized, masked, parallel design supports a direct vehicle comparison during the controlled period. Its open-label crossover extension raises a different interpretive issue: once both original groups receive ruxolitinib, extension outcomes no longer preserve a vehicle-controlled comparison. Clear separation of those periods helps prevent an extension result from being mistaken for continued randomized evidence.

Finally, this record shows the importance of distinguishing sponsor-reported methods from simple recalculations, and of recognizing what the record does not explain. The primary estimate is reported, but the detailed analysis plan, missing-data procedures, multiplicity approach, and original sample-size justification are not. That distinction helps readers interpret the numerical evidence without treating unreported design details as known.

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, so the enrolled total of 186 cannot be evaluated against the trial’s intended assumptions from this record alone. The planning illustrations based on the observed effect are separate from the trial’s original design and should not be used to infer the study’s planned power.

Important analysis details are also not reported, including a detailed statistical analysis plan, the handling of missing Week 16 outcomes, sensitivity analyses, and a multiplicity strategy for the numerous secondary outcomes. The primary endpoint’s ITT population is defined, but that alone does not explain how unavailable outcome assessments were treated.

The primary outcome is a thresholded investigator assessment. It provides a responder proportion but does not preserve all information in the underlying severity scale or describe the full range of participant experience. Numerical results for the listed secondary itch and pain measures are not reported in the registry record, so the breadth of the primary finding across symptoms cannot be assessed from these results.

The extension is open-label and crosses the vehicle group over to ruxolitinib. It therefore cannot provide a continuing randomized comparison against vehicle. The safety summary also uses different group denominators, including a ruxolitinib denominator larger than the original randomized group, and does not establish whether individual serious events were caused by treatment. These features limit causal interpretation of the extension and safety summaries beyond what the controlled primary comparison supports.

The record describes adults with moderate to severe chronic hand eczema, so applicability beyond that population is uncertain. It does not report comparative outcomes against other active treatments or follow-up beyond the stated study periods.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Topical Ruxolitinib Evaluation in Chronic Hand Eczema — NCT05906628.
• Registry record last updated 2025-07-31; status last verified 2025-07.
• Results first posted 2025-07-31.
• 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

NCT05906628 is a completed randomized, triple-masked, parallel-group phase 2 trial of ruxolitinib cream versus vehicle in adults with chronic hand eczema. Enrollment was 186. The initial controlled treatment period lasted 16 weeks and was followed by a 16-week open-label extension with crossover from vehicle to ruxolitinib.

The primary endpoint was IGA-CHE treatment success at Week 16, defined as a score of 0 or 1 with at least a 2-step improvement from baseline. Reported success was 53.2% in the ruxolitinib-assigned group and 10.9% in the vehicle-assigned group. The sponsor reported an odds ratio of 9.82 and a response-rate difference of 42.5, each with a 95% confidence interval. The record also includes safety summaries and lists secondary itch and pain outcomes, but numerical results for those secondary efficacy measures are not reported in the registry record.