A Study to Investigate Efficacy and Safety With LEO 90100 Compared With Daivobet® Ointment in Adult Chinese Subjects With Stable Plaque Psoriasis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Investigate Efficacy and Safety With LEO 90100 Compared With Daivobet® Ointment in Adult Chinese Subjects With Stable Plaque Psoriasis (NCT05919082), a randomized phase 3 study. The primary outcome is Percentage of Participants With Physician's Global Assessment of Disease Severity (PGA) Score of 0 (Clear) or 1 (Almost Clear) at Day 29, With at Least a 2-point Reduction From Baseline.

2. Clinical Question

The trial’s primary comparison concerns the proportion of participants meeting this combined endpoint after the treatment period. The registry reports 50.0% for LEO 90100 and 42.4% for Daivobet® ointment. These are group-level percentages; they do not describe the experience of every participant or establish why an individual did or did not meet the endpoint.

The registry also reports secondary outcomes based on improvement in the modified Psoriasis Area and Severity Index (mPASI), along with treatment-emergent adverse events. Those outcomes provide additional information about psoriasis severity and safety, but they are separate from the primary question. The trial is completed. The registry record does not report a longer-term comparison beyond the outcomes and timeframes posted.

3. Trial Design

This is a Phase 3, randomized, investigator-blind, active-controlled, parallel-group, multicentre trial sponsored by LEO Pharma. It enrolled 604 participants. The registry lists the study as completed, with a start date of 2023-06-21 and a primary completion date of 2024-02-23.

Participants were assigned to receive either LEO 90100 foam or Daivobet® ointment. Both treatments were applied once daily for 4 weeks. The primary endpoint was assessed on Day 29. The registry describes the primary outcome population as all randomized participants. The outcome results list 302 participants in each treatment group.

Investigator-blind means the investigators were described as masked to treatment assignment; the registry identifies masking as single. It does not report further details about which other study personnel or participants were masked, or how masking was maintained. The study used an active comparator rather than a no-treatment or placebo group, so its main contrast is between the two listed treatments under the trial conditions.

The registry record does not report the trial’s original sample-size justification, its planned statistical analysis in sufficient detail to establish all modeling choices, or whether interim analyses were planned or conducted. It also does not report a full account of missing observations, exclusions, or analysis populations beyond the primary outcome’s stated population. These omissions limit how completely the posted results can be connected to the original design and analysis plan.

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 who met the inclusion criteria and none of the exclusion criteria were enrolled to the study. All study assessments were performed as per the schedule of assessment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants.

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 Physician's Global Assessment of Disease Severity (PGA) Score of 0 (Clear) or 1 (Almost Clear) at Day 29, With at Least a 2-point Reduction From Baseline, measured over On Day 29.

The primary endpoint is the percentage of participants whose PGA score was 0 (clear) or 1 (almost clear) on Day 29 and whose score had fallen by at least 2 points from baseline. It combines a final disease-severity category with a required improvement from each participant’s starting score. The registry describes the PGA as a 5-point scale, ranging from 0 to 4, based on plaque thickening, scaling, and erythema; higher scores indicate worse outcome.

This kind of endpoint is used to express how many participants meet a defined clinical response threshold, rather than describing only an average score. Requiring both a low Day 29 score and a minimum reduction from baseline means that the endpoint incorporates the final status and the amount of change. A participant who meets one condition but not the other would not meet the combined definition.

The posted outcome is a percentage, with a 95% confidence interval for each group. It is a binary response measure at a specified timepoint: each participant either meets the endpoint definition or does not. The registry does not provide further details about the endpoint’s prespecification, handling of missing Day 29 assessments, or any sensitivity analyses. Those details are not reported in the registry record.

7. Results Posted in the Registry

• Daivobet® Ointment: 42.4% (128/302) versus 50.0% (151/302) on control; risk difference -7.6 percentage points (95% CI -15.5 to 0.3), risk ratio 0.85 (0.71–1.01); unadjusted two-proportion z-test p = 0.060.

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 With Decrease in Modified Psoriasis Area and Severity Index of at Least 75% (mPASI-75) From Baseline to Day 29

• 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:
  • Daivobet® Ointment: 53.6% (162/302) versus 63.6% (192/302) on control; risk difference -9.9 percentage points (95% CI -17.7 to -2.1), risk ratio 0.84 (0.74–0.97); unadjusted two-proportion z-test p = 0.013.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Daivobet® Ointment than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Decrease in mPASI of at Least 90% (mPASI-90) From Baseline to Day 29

• 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:
  • Daivobet® Ointment: 24.5% (74/302) versus 33.1% (100/302) on control; risk difference -8.6 percentage points (95% CI -15.8 to -1.4), risk ratio 0.74 (0.57–0.95); unadjusted two-proportion z-test p = 0.019.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Daivobet® Ointment than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the posted secondary outcomes, the group percentages follow a consistent direction: the LEO 90100 group has higher reported response proportions for both the mPASI-75 and mPASI-90 thresholds. This broad pattern is aligned with the direction of the primary endpoint estimates. It provides additional context about outcomes based on mPASI, but it does not turn those outcomes into confirmatory evidence for the primary question.

Each secondary threshold captures a different level of change, and each is a separate outcome with its own estimate and uncertainty. The secondary outcomes do not have the same status as the primary endpoint merely because their observed directions are similar. They should be interpreted in the context of the trial’s defined primary objective and the statistical plan, details of which are not fully reported in the registry record.

Testing or examining several outcomes raises multiplicity concerns: the more comparisons considered, the greater the opportunity for a result to appear notable by chance. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for the secondary endpoints. The simple recalculated secondary p-values are unadjusted and therefore carry less weight than the primary analysis. Their interpretation should be cautious and supportive rather than conclusive.

The registry also lists treatment-emergent adverse events as a secondary outcome, but these are safety observations rather than measures of psoriasis response. They are considered separately from the efficacy pattern. Overall, the consistency in the direction of the posted mPASI estimates is informative, while the lack of reported multiplicity handling and fuller analysis details limits the strength of claims based on the secondary results.

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

• Percentage of Participants With Decrease in Modified Psoriasis Area and Severity Index of at Least 75% (mPASI-75) From Baseline to Day 29
• Percentage of Participants With Decrease in mPASI of at Least 90% (mPASI-90) From Baseline to Day 29
• Number of Participants With Treatment-emergent Adverse Events (TEAEs)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either meets the response definition or does not. A group percentage is the proportion meeting that definition, expressed as a percentage. For this trial, the definition requires a PGA score of 0 or 1 at Day 29 and at least a 2-point reduction from baseline. This makes the endpoint a threshold-based response measure rather than a continuous score comparison.

What does a confidence interval describe?

A confidence interval expresses the statistical uncertainty around an estimate under the method used to calculate it. For the group percentages, the intervals indicate a range of values compatible with the observed data and calculation method. A narrower interval represents greater precision; a wider interval represents less precision. The interval does not mean that a stated percentage of individual participants had outcomes within its bounds, nor does it guarantee that the true value lies within it.

The primary group intervals are 95% confidence intervals. The interval for LEO 90100 runs from 44.36% to 55.64%; the interval for Daivobet® ointment runs from 36.81% to 47.96%. These intervals concern each group’s response percentage separately. A comparison between groups needs an interval for a contrast or an appropriate model-based result; overlap or non-overlap of separate group intervals is not a substitute for that direct comparison.

What does the odds ratio mean?

The sponsor’s reported analysis used logistic regression and expressed the treatment comparison as an odds ratio. Odds are a way of relating the number of responses to the number of non-responses. An odds ratio compares those odds between groups. A value representing no difference in odds is 1. The reported estimate is 1.4, with a 95% confidence interval from 1.01 to 1.99. The interval is on the odds-ratio scale, so it should not be interpreted as a percentage-point difference or a risk ratio.

Logistic regression can be used to model a binary outcome. The registry identifies the method and reported effect measure, but does not give the model’s covariates, full specification, or other details needed to reproduce the sponsor’s estimate. Those particulars are not reported in the registry record.

Why can the reported and recalculated analyses differ?

The simple re-calculation uses the posted summary counts and proportions to estimate an unadjusted risk difference and its uncertainty. It does not reproduce an analysis that may use a regression model or other choices not included in the summaries. Here, the re-calculated unadjusted p-value is 0.06, while the sponsor reports a logistic-regression odds ratio of 1.4 with p below 0.05. The discrepancy is recorded, so the sponsor’s own analysis takes precedence. The two results answer related but not identical statistical questions and use different effect scales and analysis methods.

A p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not quantify the size or clinical importance of an effect. A result just on either side of a conventional threshold should not be treated as a sharp boundary between meaningful and meaningless evidence. The estimate, its interval, the endpoint definition, and the analysis method all matter.

Why can over-dispersion matter?

General explanation: in some data, outcomes vary more than a statistical model assumes. This is called over-dispersion. If the model understates that variation, uncertainty can be understated and intervals may be too narrow. This is a general statistical consideration, not a reported finding about this trial. The registry record does not report a specific assessment of over-dispersion or related model diagnostics.

The same general principle applies to all model assumptions: the interpretation of an estimate depends on the analysis method being appropriate for the data and the design. The posted record names logistic regression for the sponsor’s analysis but does not provide enough detail to evaluate every assumption independently.

What is the role of the re-calculation?

A re-calculated comparison is a transparent, simple analysis based on the posted summaries. It can help readers see how the group-level data relate to a basic unadjusted contrast. It is not a substitute for the sponsor’s analysis, which takes precedence when the recorded discrepancy is present. Neither analysis alone establishes causation beyond the randomized trial’s design and conduct, and neither supplies unreported design details or addresses unreported missing-data procedures.

For the secondary binary endpoints, the same broad statistical ideas apply: each endpoint counts whether a participant crossed a defined threshold, and group percentages estimate the response proportions. Multiple outcomes create a multiplicity issue because assessing several results can increase the chance of at least one apparently notable result by chance. The registry record does not report whether or how the analysis adjusted for multiplicity, so secondary p-values should be treated as unadjusted evidence unless further analysis details are available.

11. Confidence Intervals and Precision

The group-level confidence intervals help show how precisely the response proportions are estimated. For the primary endpoint, the LEO 90100 estimate is 50.0%, with a 95% confidence interval from 44.36% to 55.64%. The Daivobet® ointment estimate is 42.4%, with a 95% confidence interval from 36.81% to 47.96%. Both intervals allow for uncertainty around the observed percentages.

For the between-group comparison, the simple unadjusted re-calculation gives a risk-difference interval that includes no difference. This is consistent with its unadjusted p-value of 0.06, but it does not replace the sponsor’s logistic-regression analysis. The sponsor reports an odds ratio of 1.4 with a 95% confidence interval from 1.01 to 1.99. That interval is relatively close to the value representing no odds difference, so the estimate’s precision is limited near that boundary. The discrepancy means the two analyses should not be collapsed into one result; the sponsor’s own analysis takes precedence.

Confidence intervals describe statistical uncertainty conditional on the calculation method and assumptions. They do not account automatically for every possible bias, such as unreported missing-data handling or deviations from the trial’s planned analysis. The registry record does not report enough detail to evaluate those issues fully. Precision should therefore be considered alongside the design, endpoint, reported analysis, and limits of the registry record.

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 original trial’s design justification. For these binary outcomes, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the 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 associated with an 80% chance of detecting the selected effect under the stated assumptions, if that effect and those assumptions were true. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm. These are conditional planning calculations, not guarantees about what a future study would find.

Rows that plan for 75% or 50% of the observed effect use smaller target effects than the row based on 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same assumptions. The figures are not observed power: they are planning illustrations and should not be read as a retrospective measure of how likely the completed trial was to detect its observed result.

The estimates are sensitive to the observed effect used as their starting point. If that estimate is imprecise or does not represent the effect expected in a new study, the resulting planning figures may not be suitable as a standalone design decision. The registry record does not report the original rationale for the enrolled number, so these illustrations should not be taken as evidence of the trial’s initial planning process.

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 = 0.500; treatment proportion p₁ = 0.424; average p̄ = 0.462.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7051 = 1.3819.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7030 = 0.5917.
4. n = (1.3819 + 0.5917)² / (-0.0762)² = 671.5, rounded up to 672 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 <- 0.5                          # control proportion
p1 <- 0.423841059602649                          # 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(5919082)
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 = 672 (80% power), 899 (90% power)
 75% of observed effect: n per arm = 1,198 (80% power), 1,603 (90% power)
 50% of observed effect: n per arm = 2,702 (80% power), 3,616 (90% power)
power.prop.test: 671.5 
Simulated power at n = 672 per arm: 0.807 (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 analysis as logistic regression, with an odds ratio of 1.4, a 95% confidence interval from 1.01 to 1.99, and a p-value below 0.05. The simple unadjusted re-calculation from the posted group summaries instead gives p = 0.06, with an interval for the risk difference that includes no difference. The methods and effect scales differ, and the registry record does not give enough detail to reproduce all choices in the sponsor’s model.

The discrepancy is flagged in the record. Under that circumstance, the sponsor’s own analysis takes precedence; the recalculated result is best understood as a basic unadjusted check rather than a correction to the reported analysis. It is useful to keep the two findings distinct: one is the registry’s reported logistic-regression result, and the other is a simple comparison calculated from group-level summaries.

The sponsor’s result remains an estimate with uncertainty, not a declaration that a treatment works or does not work. Its confidence interval is close to the value representing no odds difference. The registry record does not report enough information about the model specification, covariates, or missing-data procedures to independently assess all aspects of that analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes, including two mPASI response thresholds and treatment-emergent adverse events. When several outcomes are examined, multiplicity can make apparently notable results more likely by chance. Statistical plans may address this through an adjustment or a prespecified testing sequence. Whether either approach was planned or used is not reported in the registry record.

The record also does not report the full statistical analysis plan, whether outcomes or analyses changed after the trial began, or whether interim analyses were planned or conducted. These details matter because they help distinguish confirmatory analyses chosen in advance from additional analyses considered after observing the data. Their absence from the registry record does not establish that no such procedures existed; it means the record does not document them.

The primary outcome states that the population was all randomized participants. That is useful information about the intended analysis population, but it does not describe how missing Day 29 assessments, protocol deviations, or other incomplete observations were handled. Missing-data methods, imputation choices, sensitivity analyses, and the exact denominators used for every efficacy analysis are not reported in the registry record.

These limitations affect interpretation of both efficacy and precision. Missing-data handling can influence response proportions, while multiplicity handling affects the interpretation of secondary tests. Without the relevant details, readers cannot fully evaluate whether the reported intervals and p-values account for these issues. The sponsor’s reported primary analysis remains the recorded analysis, but the limits on its documentation should be kept in view.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: patella fracture (0.3%), gastrointestinal haemorrhage (0.3%), appendicitis (0.3%), psoriasis (0.3%).

The registry reports serious adverse events for 4 participants at risk in the LEO 90100 group and 0 in the Daivobet ointment group. The corresponding numbers listed at risk are 300 and 301. The registry lists no deaths in either group. The serious-event terms reported among the top terms are patella fracture, gastrointestinal haemorrhage, appendicitis, and psoriasis, each shown as 0.3%.

These figures describe events recorded during the trial; they do not by themselves establish that a treatment caused an event or that an event was unrelated to treatment. Serious adverse events are not interchangeable with all adverse events, and the registry separately lists other treatment-emergent adverse events affecting 53 participants in the LEO 90100 group and 39 in the Daivobet group, using the listed at-risk counts of 300 and 301.

The registry does not provide detailed event narratives, timing, exposure-adjusted rates, or a full assessment of causality. The short treatment period and the posted event counts therefore offer limited information about uncommon or longer-term harms. Safety comparisons should be read as descriptive trial observations, not as a complete assessment of safety.

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

The results describe the proportions of trial participants meeting defined response criteria after four weeks of once-daily treatment. On the primary endpoint, the posted percentages are higher for LEO 90100 than for Daivobet® ointment. The sponsor’s logistic-regression analysis reports an odds ratio of 1.4 with a 95% confidence interval from 1.01 to 1.99 and a p-value below 0.05. The simple unadjusted re-calculation does not reach that threshold, and the sponsor’s analysis takes precedence because a discrepancy is flagged.

That statistical result does not, by itself, establish the size or importance of a treatment difference for an individual. An odds ratio is not a percentage-point difference, and a p-value is not the probability that the finding is true. The confidence interval reflects uncertainty under the reported model and does not remove possible bias or unreported limitations in analysis and follow-up.

The findings apply to the trial population and its conditions: adult Chinese subjects with stable plaque psoriasis, assigned to one of the two active treatments and assessed at the posted timepoints. They do not establish outcomes after treatment ends, long-term safety, or results in populations not described by the registry. The record does not report longer-term follow-up results.

The secondary mPASI outcomes have a direction consistent with the primary group percentages, but multiplicity handling is not reported. They therefore offer supporting context rather than definitive additional evidence. The safety counts are also descriptive and should not be treated as proof that an event was or was not caused by treatment. Overall, the posted data support a careful reading of trial-specific estimates, their uncertainty, and the limits of the available record, rather than a broad clinical conclusion.

18. Why This Trial Matters Statistically

This trial illustrates why an endpoint definition matters. The primary outcome is not simply a low PGA score: it requires both a score of 0 or 1 at Day 29 and at least a 2-point reduction from baseline. A clear definition makes the response proportion interpretable, while also making clear that participants who meet only one part of the condition are not counted as responders.

It also shows why the choice of effect measure and analysis method matters. The registry reports an odds ratio from logistic regression, while a simple recalculation from the posted summaries uses an unadjusted risk-difference comparison. The discrepancy means the two analyses should be reported distinctly, with the sponsor’s analysis taking precedence rather than allowing a simple recalculation to stand in for the trial’s reported method.

Precision is part of interpretation, not an optional extra. The confidence intervals show that the group percentages are estimates with uncertainty, and the sponsor’s interval lies close to the value representing no odds difference. The direction of the point estimates alone does not capture that uncertainty.

Finally, the secondary outcomes and safety observations show why results need context. Multiple secondary comparisons can complicate interpretation when the multiplicity plan is not reported, and short-term adverse-event counts do not describe longer-term safety. The registry record’s gaps about missing data and the full statistical plan limit how completely readers can assess the analysis. These are practical reasons to consider design, endpoint, method, uncertainty, and reporting together.

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 provides limited information about several aspects of trial conduct and analysis. Although the primary population is described as all randomized participants, the record does not explain how missing endpoint assessments, protocol deviations, or incomplete observations were handled. The exact analysis population and denominators for every efficacy analysis are not fully described.

The sponsor’s primary analysis is identified as logistic regression, but the model specification and any covariates are not reported. The record also does not report the original sample-size justification, whether interim analyses were planned or conducted, or how multiplicity across the primary and secondary outcomes was addressed. These omissions limit independent assessment of the analysis plan and the secondary findings.

The primary endpoint is measured on Day 29 after a 4-week treatment period. Longer-term outcomes are not reported in the registry record, so the posted efficacy and safety data do not establish durability or longer-term event patterns. The safety listing gives counts and selected serious-event terms, but not detailed narratives, timing, exposure-adjusted analyses, or full causality assessments.

The trial is investigator-blind, but the registry does not report which other groups were masked or how masking was maintained. It is also an active-controlled study, so the recorded comparison concerns the two active treatments under the study conditions rather than either treatment compared with no treatment. These limitations do not invalidate the reported estimates, but they define what can and cannot be concluded from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Investigate Efficacy and Safety With LEO 90100 Compared With Daivobet® Ointment in Adult Chinese Subjects With Stable Plaque Psoriasis — NCT05919082.
• Registry record last updated 2026-04-06; status last verified 2025-03.
• Results first posted 2025-03-21.
• 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

NCT05919082 is a completed Phase 3 randomized, investigator-blind, active-controlled, parallel-group, multicentre trial sponsored by LEO Pharma. It enrolled adult Chinese subjects with stable plaque psoriasis and compared LEO 90100 foam with Daivobet® ointment, each used once daily for 4 weeks.

The primary endpoint was the percentage with a PGA score of 0 or 1 at Day 29 and at least a 2-point reduction from baseline. The posted percentages were 50.0% for LEO 90100 and 42.4% for Daivobet® ointment. The sponsor reported a logistic-regression odds ratio of 1.4, with a 95% confidence interval from 1.01 to 1.99 and a p-value below 0.05. A simple unadjusted re-calculation differs, so the sponsor’s analysis takes precedence.

Secondary mPASI outcomes follow a similar direction in the group percentages, while multiplicity handling, missing-data procedures, and several details of the analysis plan are not reported in the registry record. Safety counts are descriptive and do not establish causation or longer-term risk.