A 32-week Trial to Evaluate the Efficacy and Safety of Tralokinumab in Subjects With Moderate-to-severe Atopic Hand Eczema Who Are Candidates for Systemic Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A 32-week Trial to Evaluate the Efficacy and Safety of Tralokinumab in Subjects With Moderate-to-severe Atopic Hand Eczema Who Are Candidates for Systemic Therapy (NCT05958407), a randomized phase 3 study. The primary outcome is Percentage of Participants With IGA-AHE Score of 0 (Clear) or 1 (Almost Clear).

2. Clinical Question

The study asks whether the proportion meeting this specific skin-severity threshold at Week 16 differs between the tralokinumab and placebo groups. It is a comparison of the percentage of responders, rather than a comparison of average scores or a measure of time until an event. The registry also lists assessments of hand eczema severity, itch, pain, health status, and quality of life; the primary question is narrower and focuses on the IGA-AHE response threshold.

The trial enrolled participants with atopic hand eczema who were candidates for systemic therapy. Its posted primary result describes the Week 16 response in the Full Analysis Set. The registry reports separate group percentages and confidence intervals, as well as a treatment-difference analysis. These quantities address related but distinct questions: the group percentages describe the response observed in each arm, while the treatment difference describes the estimated contrast between arms.

3. Trial Design

This was a randomized, double-blind, parallel-group Phase 3b interventional trial of tralokinumab and placebo. The registry lists an enrollment of 235 participants and identifies LEO Pharma as the sponsor. The study status is completed. The listed start date is 2023-08-28, and the primary completion date is 2025-05-05.

During the first 16 weeks after screening, participants received tralokinumab or placebo every second week. This was the double-blind comparison period and is the period relevant to the primary Week 16 result. Afterward, participants in both groups received open-label tralokinumab every second week for 16 weeks. The record describes an additional safety-monitoring period of 4 weeks after treatment. The participant-facing summary describes a trial lasting up to 40 weeks for each participant, with up to 15 visits, including 3 by phone.

The tralokinumab arm is described as receiving treatment for 32 weeks: 16 weeks during the double-blind period and 16 weeks during the open-label period. The placebo arm received placebo for 16 weeks before rolling over to open-label tralokinumab. Consequently, the randomized placebo comparison pertains to the initial period; later observations occur after the groups no longer have the same treatment contrast.

The official title calls the study adaptive, but the specific adaptive features, decision rules, or any resulting changes to the design are not reported in the registry record. The original sample-size rationale and the trial’s planned statistical assumptions are also not reported in the registry record. The registry does identify the primary analysis population and the sponsor’s logistic-regression method for the primary treatment comparison.

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 randomized 2:1 to treatment with tralokinumab or placebo.

Double-blinded Period

Reasons for not completing this period:

Transfer to Open-label Treatment

Reasons for not completing this period:

Open-label Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analyzed population: Full Analysis Set (FAS) - all randomized participants who were exposed to at least dose of investigational medicinal product (IMP).

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 IGA-AHE Score of 0 (Clear) or 1 (Almost Clear), measured over At Week 16.

The primary endpoint is the percentage of participants with an IGA-AHE score of 0, clear, or 1, almost clear, at Week 16. The IGA-AHE is an investigator assessment of atopic hand eczema severity on a 5-point scale ranging from 0, clear, to 4, severe. The endpoint converts that graded assessment into a binary response: participants either meet the stated 0-or-1 threshold or they do not.

This type of endpoint is useful when a study aims to report the share of participants reaching a defined clinical status. It gives a direct, interpretable group-level quantity: the percentage meeting the threshold. The threshold also makes the endpoint different from a mean change in severity. A participant just meeting the response definition and one with a lower score both count as responders, while people above the threshold are classified as nonresponders for this endpoint. That simplification can make results easier to communicate, but it does not show the full distribution of scores or the size of change for each participant.

The registry reports the result at Week 16, when the randomized, double-blind comparison was in place. The posted analysis population is the Full Analysis Set, defined as all randomized participants exposed to at least one dose of investigational medicinal product. How missing Week 16 assessments were handled is not reported in the registry record.

7. Results Posted in the Registry

• Tralokinumab: 39.7% (62/156) versus 10.1% (8/79) on control; risk difference 29.6 percentage points (95% CI 19.5 to 39.8), risk ratio 3.92 (1.98–7.78); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

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

Percentage of Participants Having a ≥2-point Reduction in IGA-AHE Score

• 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:
  • Tralokinumab: 49.4% (77/156) versus 17.7% (14/79) on control; risk difference 31.6 percentage points (95% CI 20.1 to 43.1), risk ratio 2.79 (1.69–4.60); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Tralokinumab than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Having a Decrease in HECSI of at Least 75% (HECSI-75)

• 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:
  • Tralokinumab: 62.2% (97/156) versus 31.6% (25/79) on control; risk difference 30.5 percentage points (95% CI 17.8 to 43.3), risk ratio 1.96 (1.39–2.78); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Tralokinumab than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Having a Decrease in HECSI of at Least 50% (HECSI-50)

• 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:
  • Tralokinumab: 78.2% (122/156) versus 48.1% (38/79) on control; risk difference 30.1 percentage points (95% CI 17.3 to 42.9), risk ratio 1.63 (1.27–2.07); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Tralokinumab than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The detailed secondary results shown in the tables cover an IGA-AHE improvement threshold and HECSI response thresholds at Week 16. Across those posted comparisons, the tralokinumab group has higher response percentages than the placebo group, and the sponsor-reported logistic-regression analyses report p < .001. This direction is consistent with the primary response result, but the secondary outcomes measure different aspects or thresholds of eczema severity and should not be treated as duplicates of the primary endpoint.

The registry lists 21 secondary outcomes, including measures of HECSI response and change, itch, and pain. Numerical results for all of those outcomes are not reported in the registry record here, so the pattern across the full secondary outcome set cannot be assessed from the detailed results. The tabulated secondary findings should be read on their own terms and alongside their confidence intervals.

Secondary results generally carry less confirmatory weight when many outcomes are examined and the multiplicity strategy is not reported in the registry record. Testing several endpoints can increase the chance that at least one appears statistically notable by chance. A prespecified testing hierarchy or multiplicity adjustment can address this concern, but the record does not describe such a procedure. This does not make the secondary findings uninformative; it means that they are supportive evidence rather than a substitute for the primary analysis.

The secondary outcomes may broaden the description of response beyond the IGA-AHE clear-or-almost-clear threshold. They do not, by themselves, resolve questions about the full score distribution, durability beyond the randomized comparison period, or how missing measurements were handled. Those interpretations require details that are not reported in the registry record.

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

• Percentage of Participants Having a ≥2-point Reduction in IGA-AHE Score
• Percentage of Participants Having a Decrease in HECSI of at Least 75% (HECSI-75)
• Percentage of Participants Having a Decrease in HECSI of at Least 50% (HECSI-50)
• Percentage of Participants Having a Decrease in HECSI of at Least 90% (HECSI-90)
• Percentage Change in HECSI Score
• Percentage of Participants With Reduction in HESD Itch Score (Weekly Average) of ≥4 Points
• Percentage Change in HESD Itch Score (Weekly Average)
• Percentage of Participants With Reduction in HESD Pain Score (Weekly Average) of ≥4 Points

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either had an IGA-AHE score of 0 or 1 at Week 16 or did not. The registry reports the percentage of responders in each group and 95% confidence intervals for those percentages. It also reports a treatment difference using logistic regression. The tables and plots on this page present these results alongside an unadjusted recalculation from posted summary statistics.

What does a response percentage show?

A response percentage is the proportion of participants in a group who meet the endpoint definition. Here, the definition is an IGA-AHE score of clear or almost clear at Week 16. This quantity is easy to interpret in relation to the endpoint threshold, but it discards some information: it does not distinguish between different scores within the responder category, and it does not describe the amount of change for participants who remain above the threshold.

A binary endpoint also depends on the selected cutoff. Someone just inside the response definition is counted the same way as someone with a lower score, while someone just outside it is counted as a nonresponder. The IGA-AHE scale itself is described in the registry, but the primary endpoint is the share meeting the 0-or-1 criterion rather than the full score distribution.

How should the confidence intervals be read?

A confidence interval expresses statistical uncertainty around an estimate under the method used to construct it. For the arm-level percentages, the reported 95% intervals describe uncertainty in the response percentage for each group. For the treatment difference, the interval describes uncertainty in the estimated contrast between groups. A narrower interval indicates greater precision for that particular estimate; a wider interval indicates more uncertainty. The interval does not guarantee that the true value lies within its limits, and it is not a range containing a stated percentage of individual participant outcomes.

For the primary endpoint, the sponsor reports a logistic-regression treatment difference in percentage with a 95% confidence interval. The regression method can account for the model structure used in the sponsor’s analysis, but the covariates and detailed model specification are not reported in the registry record. The posted recalculation is unadjusted and uses the reported summary statistics, so it is not interchangeable with the sponsor’s regression estimate.

What does the p-value tell us?

The sponsor reports p < .001 for the primary comparison. In general, a p-value describes how incompatible the observed data are with a specified null hypothesis under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not measure effect size or clinical importance. The estimated treatment difference and its interval provide information about magnitude and precision that the p-value alone does not provide.

The registry identifies the sponsor’s method as logistic regression and the analysis type as superiority. The exact null hypothesis wording, covariate adjustments, missing-data procedures, and any sensitivity analyses are not reported in the registry record. Those details matter for fully assessing how the model handled the trial data, so they cannot be inferred from the method label alone.

Why show an unadjusted recalculation?

A simple recalculation from posted arm-level summary statistics can help readers see the scale of the group contrast without relying only on a model-based report. It is a descriptive cross-check, not a replacement for the sponsor’s analysis. The sponsor’s result is based on logistic regression; the recalculation is unadjusted. Different methods can give slightly different estimates and intervals, even when they analyze the same trial question. The registry does not mark a discrepancy between the posted results and the recalculation.

Interpret the recalculation as one way to summarize the posted data, not as evidence that the sponsor’s model was reproduced. The recalculation does not recover participant-level information, model covariates, or unreported choices in the analysis. It also cannot address the consequences of missing outcome data unless those procedures and data are available.

Why do secondary analyses need extra care?

The registry lists 22 outcome measures and 16 analyses. When several outcomes or comparisons are examined, the chance of finding a small p-value by chance can increase if each is treated as a separate confirmatory test. A multiplicity plan may limit this issue by specifying how tests are ordered or how significance thresholds are handled. Such a plan is not reported in the registry record. Therefore, the posted secondary p-values should be considered in the context of the primary endpoint and not automatically treated as independent confirmatory findings.

General statistical considerations also apply to binary outcomes. The observed percentages depend on the number of participants with usable endpoint information and on how missing assessments are classified or modeled. The analysis population is defined in the registry, but the Week 16 missing-data method is not reported in the registry record. Without those details, readers cannot fully assess sensitivity to assumptions about participants whose endpoint status is unavailable.

11. Confidence Intervals and Precision

The primary arm-level confidence intervals are 32.2 to 47.9 for tralokinumab and 5.1 to 20.2 for placebo. The sponsor’s reported treatment-difference interval is 19.2 to 40.0. These intervals describe uncertainty in different quantities: the first two concern response percentages within each group, while the third concerns the estimated contrast between groups.

The treatment-difference interval does not include zero. This is consistent with the sponsor’s reported p-value of p < .001 for the primary analysis. The interval is also useful because it shows a range of effect estimates compatible with the data under the analysis assumptions, rather than presenting only a single point estimate. Its width reflects uncertainty, not variation in individual responses.

Confidence intervals are not a substitute for examining the underlying endpoint definition, analysis population, or missing-data handling. The Full Analysis Set includes randomized participants exposed to at least one dose, but the method for handling missing Week 16 assessments is not reported in the registry record. That information could affect interpretation of the precision and robustness of the reported estimate.

The table and plot allow readers to compare the arm-level estimates and the treatment contrast visually. They should be read as estimates from this trial, not as guarantees about a future sample or about every participant. Precision also does not establish clinical importance: the interval quantifies statistical uncertainty in the measured endpoint, while the registry does not provide a threshold for deciding what size of difference would be clinically important.

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

The 80% power column gives the illustrative number of participants per arm under those assumptions for an analysis to have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding illustration for a 90% chance. These are planning quantities, not guarantees about what a study with those group sizes would find; uncertainty, outcome rates, analysis methods, and departures from assumptions can all matter.

Rows that use a smaller fraction of the observed effect require more participants per arm in the illustration. This reflects a general statistical principle: smaller differences are harder to distinguish from sampling variation, all else being equal. The curve presents the planning relationship visually, while the table provides selected planning values. Neither represents an observed power calculation for this completed trial.

These illustrations should not be taken as the trial’s planned enrollment target or as proof that the trial was adequately or inadequately sized. The registry enrollment is reported separately, and the original sample-size rationale is not reported in the registry record. The planning estimates simply show how the required group size changes under the stated assumptions and effect scenarios.

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 = 0.101; treatment proportion p₁ = 0.397; average p̄ = 0.249.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6118 = 1.1992.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5749 = 0.4838.
4. n = (1.1992 + 0.4838)² / (0.2962)² = 32.3, rounded up to 33 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 <- 0.10126582278481                          # control proportion
p1 <- 0.397435897435897                          # 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(5958407)
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 = 33 (80% power), 43 (90% power)
 75% of observed effect: n per arm = 53 (80% power), 70 (90% power)
 50% of observed effect: n per arm = 103 (80% power), 137 (90% power)
power.prop.test: 32.3 
Simulated power at n = 33 per arm: 0.834 (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 logistic regression, with a treatment difference in percentage of 29.6, a 95% confidence interval from 19.2 to 40.0, and p < .001. This is the sponsor’s model-based analysis and is the principal reported comparison for the primary endpoint.

The recalculation is a simple, unadjusted analysis from the posted summary statistics. It offers a separate view of the observed group contrast, but it does not reproduce the regression model or its assumptions. The two approaches therefore should not be treated as identical estimates. The registry does not flag a discrepancy, and the reported group percentages and sponsor analysis show the same broad direction of contrast.

For interpretation, give priority to the sponsor’s reported analysis when describing the trial’s formal result, while using the recalculation as a transparent descriptive check. The registry record does not report enough detail about regression covariates, missing-data handling, or sensitivity analyses to reconstruct the sponsor’s model independently. The reported confidence interval and p-value should therefore be attributed to the sponsor analysis rather than to the unadjusted recalculation.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 22 outcome measures and 16 analyses. Examining multiple outcomes can create a multiplicity problem: if each test is interpreted in isolation, the overall chance of at least one false-positive result may be greater than the nominal level for a single test. A prespecified hierarchy, adjustment, or other multiplicity strategy can help control that issue. The multiplicity procedure for this trial is not reported in the registry record.

The primary endpoint is identified, and the sponsor’s analysis is described as logistic regression. However, the registry record does not report the full statistical analysis plan, model covariates, or a testing sequence for secondary outcomes. The listed secondary findings should therefore be interpreted as additional evidence, with less weight for confirmatory claims when the family-wise testing approach is unknown.

The Full Analysis Set is described as randomized participants who received at least one dose of investigational medicinal product. This definition clarifies which participants are eligible for the primary analysis, but it does not explain the treatment of participants without a Week 16 assessment. The missing-data method, assumptions about missing outcomes, and sensitivity analyses are not reported in the registry record.

Missing data matter because the percentage responding depends on who contributes an evaluable endpoint and how unavailable outcomes are handled. Different methods can imply different assumptions about participants whose results are missing. Without the method and relevant sensitivity analyses, readers cannot determine how robust the estimates are to those assumptions. The posted confidence intervals quantify uncertainty under their analysis methods; they do not, on their own, resolve uncertainty from unreported missing-data decisions.

The official title describes the study as adaptive, but the registry record does not report the specific adaptations, interim decision rules, or whether any design changes occurred. Those details, along with the original sample-size rationale, are not reported in the registry record. No conclusions about the trial’s adaptive procedures or their effect on error control can be drawn from the title alone.

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 detachment (1.3%), condition aggrevated (1.3%), myositis (0.6%), alcoholic seizure (0.6%), hypertensive crisis (0.6%).

During the double-blind period, the registry reports serious adverse events in 3 of 156 participants at risk in the tralokinumab group and 1 of 79 in the placebo group. It reports no deaths in either group. During the open-label tralokinumab period, serious adverse events are reported in 4 of 214 participants at risk, with no deaths listed. The open-label period is a different treatment phase and should not be read as a randomized comparison with placebo.

The registry also lists other adverse events in 50 of 156 participants at risk in the double-blind tralokinumab group, 19 of 79 in the double-blind placebo group, and 31 of 214 in the open-label tralokinumab group. These are descriptive counts for the specified periods. They do not establish that one treatment caused or prevented an event, and the different periods and group structures limit direct comparisons.

Listed serious-event terms include Retinal detachment, Condition aggrevated, Myositis, Alcoholic seizure, Hypertensive crisis, and Enteritis, with the percentages shown in the safety table. The registry does not provide further context for interpreting these terms. Counts and listed terms should be read as safety reporting, not as a formal estimate of comparative risk.

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

The posted primary result shows a higher Week 16 percentage meeting the IGA-AHE clear-or-almost-clear threshold in the tralokinumab group than in the placebo group. The sponsor’s logistic-regression estimate of the treatment difference has a 95% confidence interval above zero and is reported with p < .001. This is evidence of a difference in the measured endpoint under the sponsor’s analysis.

That statement is limited to the outcome definition, population, and time point reported. The endpoint is a binary threshold on the IGA-AHE scale; it does not capture every dimension of atopic hand eczema or describe the magnitude of improvement for each participant. It also does not establish how long any response lasted after the Week 16 comparison. After Week 16, the placebo group moved to open-label tralokinumab, so the later period does not retain the same randomized placebo contrast.

A statistically distinct result is not automatically a measure of clinical importance. The registry does not provide a threshold for judging the smallest difference that would be meaningful to participants, nor does the primary percentage describe each individual’s experience. The confidence interval gives a range of estimates compatible with the data under the reported analysis; it is not a prediction interval for future participants or studies.

The result also does not settle safety questions. The serious adverse event figures are descriptive counts across treatment periods, and the registry information does not establish comparative causal effects. Nor does the primary finding establish that every listed secondary outcome improved, since outcome-specific results and multiplicity procedures are not fully.

In short, the registry reports a Week 16 difference in the percentage meeting a defined severity threshold. Interpretation beyond that endpoint requires caution about the analysis details, missing-data procedures, multiplicity, and the limits of a registry summary.

18. Why This Trial Matters Statistically

This trial illustrates how a threshold-based endpoint can turn a graded clinical assessment into a group-level response percentage. That makes the primary result readily interpretable, while also highlighting a trade-off: the binary endpoint does not retain all information in the underlying IGA-AHE scale. Readers can see the responder proportion and the treatment contrast, but not the full distribution of severity scores from this result alone.

The record also offers an example of why estimates, intervals, and p-values should be read together. The group percentages describe observed response levels, the sponsor’s treatment difference summarizes the contrast, the confidence interval communicates precision, and the p-value addresses compatibility with a null hypothesis under the analysis. Each contributes different information; none alone gives a complete account.

The distinction between the sponsor’s regression analysis and the unadjusted recalculation is another useful statistical lesson. Summary-statistic recalculations can make a result more transparent, but they cannot reproduce a participant-level model or fill in unreported assumptions. Treating the calculations as complementary rather than interchangeable helps keep the interpretation aligned with the evidence available.

Finally, the record shows why multiplicity, missing data, and treatment-period structure matter. There are multiple outcome measures, but the multiplicity strategy and Week 16 missing-data handling are not reported in the registry record. The randomized placebo comparison applies to the double-blind period; after crossover to open-label treatment, the comparison has a different meaning. These considerations are central to judging what the posted result can support.

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 leaves several details unavailable for evaluating the result fully. Although the title describes an adaptive trial, the particular adaptations and decision rules are not reported in the registry record. The trial’s original sample-size rationale and its planned design assumptions are also not reported in the registry record.

The primary analysis population is defined, but the Week 16 missing-data method, assumptions for unavailable assessments, and sensitivity analyses are not reported in the registry record. These details are important because the endpoint is a responder percentage and the estimate can depend on how participants without an observed assessment are handled.

The sponsor’s method is identified as logistic regression, but its full specification, including any covariates, is not reported in the registry record. The unadjusted recalculation cannot recover those model details and should not be used as a substitute for the sponsor analysis.

The registry lists many secondary measures, but the multiplicity approach is not reported in the registry record. Detailed numerical results are not available for every listed secondary outcome, limiting assessment of the overall pattern across endpoints. The primary endpoint also represents one threshold and one time point; it does not describe the full scale distribution or establish the persistence of responses.

Finally, the study changes treatment after the double-blind period: the placebo group rolls over to open-label tralokinumab. Later results therefore do not provide the same randomized comparison as the Week 16 endpoint. Safety counts from the double-blind and open-label periods should likewise be read separately and descriptively.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A 32-week Trial to Evaluate the Efficacy and Safety of Tralokinumab in Subjects With Moderate-to-severe Atopic Hand Eczema Who Are Candidates for Systemic Therapy — NCT05958407.
• Registry record last updated 2026-10-22; status last verified 2026-07.
• Results first posted 2026-08-05.
• 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

This completed randomized, double-blind, parallel-group Phase 3b trial evaluated tralokinumab versus placebo in participants with moderate-to-severe atopic hand eczema who were candidates for systemic therapy. The registry lists an enrollment of 235 and identifies LEO Pharma as the sponsor.

The primary endpoint was the percentage with an IGA-AHE score of 0 or 1 at Week 16. The sponsor reports a logistic-regression treatment difference of 29.6, with a 95% confidence interval from 19.2 to 40.0 and p < .001. Participants assigned to placebo moved to open-label tralokinumab after the initial 16-week double-blind period.

The registry also reports secondary outcomes and safety counts. Multiplicity procedures, Week 16 missing-data handling, and the detailed adaptive design features are not reported in the registry record. The results should be interpreted in light of those unreported analysis details and the endpoint’s specific threshold definition.