A Psoriasis Plaque Test Study With LEO 90100 Cutaneous Spray, Ointment, in Psoriasis Vulgaris: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Psoriasis Plaque Test Study With LEO 90100 Cutaneous Spray, Ointment, in Psoriasis Vulgaris (NCT01347255), a randomized phase 2 study. The primary outcome is Absolute Change in Total Clinical Score (TCS) of Clinical Signs (Sum of Erythema, Scaling and Infiltration) at End of Treatment Compared to Baseline.

2. Clinical Question

3. Trial Design

This completed phase 2 study is titled “A Psoriasis Plaque Test Study With LEO 90100 Cutaneous Spray, Ointment, in Psoriasis Vulgaris.” The registry describes it as randomized, single-masked and single-group, with enrollment of 24. It lists four treatment entries: LEO 90100 cutaneous spray, ointment; the vehicle with betamethasone; the vehicle alone; and Daivobet® ointment. Each reported primary-outcome group has a stated sample size of 24. The registry record does not explain how these four entries fit the single-group model or how randomization was implemented.

The study’s purpose was to evaluate the anti-psoriatic effect of LEO 90100 using a psoriasis plaque test modified from a method attributed in the study summary to KJ Dumas and JR Scholtz. The primary analysis population is called intra-individual. That description is important, but it does not specify whether treatment observations were paired within each participant, how plaques or treatment sites were assigned, or what statistical method accounted for any within-person dependence. Those design and analysis details are not reported in the registry record.

The primary endpoint compares baseline on Day 1 with Day 29, the end of treatment. The listed secondary outcomes include changes in clinical sign scores, TCS by visit, echo-poor band thickness, and total skin thickness. Numerical secondary results are available for echo-poor band thickness; results for the other listed outcomes are not reported in the registry record. The start and primary-completion entries are in 2011, and the study status is completed. Further details about recruitment, follow-up, protocol deviations and participant flow are not reported in the registry record.

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: The study was conducted with 3 successive individual phases: * Screening Phase (washout if applic.). A medical examination was performed at screening which took place 1-21 days before the start of the treatment phase (Day 1). * Treatment Phase (All patients (N=24) received all investigational medicinal products) * Follow-up Phase (if applic.)

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intra-individual analysis population

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Intra-individual baseline analysis population

6. Primary Endpoint

The registry lists the primary outcome as Absolute Change in Total Clinical Score (TCS) of Clinical Signs (Sum of Erythema, Scaling and Infiltration) at End of Treatment Compared to Baseline, measured over Day 1 (Baseline)/Day 29.

The primary endpoint is the absolute change in TCS at the end of treatment compared with baseline. TCS sums three clinical signs—erythema, scaling and infiltration—and ranges from 0, where all signs are absent, to 9, where all signs are severe. The measure turns these separate signs into a single score that can be compared over time and across the listed treatment entries.

A negative change indicates that the recorded score was lower at Day 29 than at baseline; a more negative mean therefore represents a larger average reduction in the score. This is a score-based description, not a direct measure of every aspect of psoriasis or of how participants felt or functioned. The registry record does not report a threshold for a clinically important change, nor does it explain how the three component signs were rated or combined beyond stating that they are summed.

Using a baseline-to-endpoint change makes the result interpretable as change during the study period, rather than as an end-of-treatment score alone. However, a mean change does not show how many individuals improved, whether changes varied substantially among individuals, or whether the result applies beyond the plaque-test setting. Those details are not reported in the registry record.

7. Results Posted in the Registry

• LEO 90100 Cutaneous Spray, Ointment: mean -6.00 versus -4.96 on control; difference -1.04 (95% CI -1.94 to -0.14), standardized effect d = -0.66; z-test p = 0.023.
• LEO 90100 Cutaneous Spray, Ointment, Vehicle: mean -1.88 versus -4.96 on control; difference 3.08 (95% CI 2.21 to 3.95), standardized effect d = 2.01; z-test p = <0.001.
• Daivobet® Ointment: mean -5.25 versus -4.96 on control; difference -0.29 (95% CI -1.32 to 0.74), standardized effect d = -0.16; z-test p = 0.580.

8. Secondary Efficacy Endpoints

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

Change From Baseline in Echo-poor Band Thickness at End of Treatment

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • LEO 90100 Cutaneous Spray, Ointment: mean -0.57 versus -0.45 on control; difference -0.12 (95% CI -0.25 to 0.01), standardized effect d = -0.52; z-test p = 0.072.
  • LEO 90100 Cutaneous Spray, Ointment, Vehicle: mean -0.12 versus -0.45 on control; difference 0.33 (95% CI 0.20 to 0.46), standardized effect d = 1.46; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LEO 90100 Cutaneous Spray, Ointment and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for LEO 90100 Cutaneous Spray, Ointment, Vehicle than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary measures covering clinical sign scores, TCS across visits, echo-poor band thickness and total skin thickness. The numerical secondary result included in the record is for change in echo-poor band thickness from baseline to Day 29. Its direction broadly aligns with the primary endpoint in that the active combination has a larger mean reduction than the vehicle with betamethasone, while the vehicle-alone group shows a smaller reduction. This directional consistency is descriptive; the measures are not interchangeable, and one cannot establish the primary finding by treating a related secondary outcome as independent confirmation.

The other listed secondary outcomes do not have numerical results reported in the registry record. That limits the ability to assess whether the overall pattern across clinical signs, visits and skin measurements was consistent, or whether it varied by measure or time. It also prevents a full evaluation of the study’s secondary-outcome evidence.

The recalculated secondary comparison for echo-poor band thickness is unadjusted. Its interval reaches across zero and its unadjusted p-value is 0.072 for LEO 90100 versus vehicle with betamethasone; the vehicle-alone comparison has an unadjusted p-value of <0.001. These calculations should not be given the same evidential weight as a prespecified, multiplicity-controlled analysis. The record does not report whether secondary outcomes were prespecified in a hierarchy, whether any adjustment was planned, or whether these were exploratory.

As a general statistical principle, examining several outcomes and comparisons creates more opportunities for apparently notable results to arise by chance. Without a reported multiplicity strategy, individual unadjusted secondary results are best read as supportive or exploratory descriptions, not as stand-alone confirmation. The registry record does not provide enough information to determine the intended role of each secondary measure.

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

• Change in Clinical Sign Scores
• Changes in Total Clinical Score (TCS) by Visit
• Change From Baseline in Echo-poor Band Thickness at End of Treatment
• Changes in Total Skin Thickness

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a score that can take values across the stated TCS scale, and the registry reports a mean change with a standard deviation for each treatment entry. A mean describes the average observed change in a group; a standard deviation describes how spread out individual changes are around that average. The standard deviation is not the uncertainty interval for the mean, and it does not say that every participant had a change close to the group mean.

What does the mean difference represent?

The recalculated comparisons subtract the mean change in the reference group from the mean change in the named comparison group. The reference for the primary comparisons is the vehicle with betamethasone. Thus, the sign of a contrast depends on the order of subtraction as well as on the direction of change. Since decreases in TCS are negative changes, a contrast below zero indicates a more negative mean change in the comparison group; a contrast above zero indicates a less negative mean change in that group. Reading the contrast alongside both group means prevents a sign from being mistaken for an improvement or worsening on its own.

These are unadjusted recalculations from the posted means, standard deviations and sample sizes. They do not include an adjustment for other variables or for the multiple treatment comparisons. The registry record lists an intra-individual analysis population, but the method used to account for any correlation between observations from the same person is not reported. A simple comparison based on group summaries may not reflect a paired analysis. The registry entries do not include the within-person covariance needed to assess a paired contrast from the summaries alone, nor do they report the sponsor’s statistical model.

Why does the confidence interval matter?

A confidence interval conveys a range of values compatible with the estimate under the calculation’s assumptions. It expresses sampling uncertainty, not the range of individual participant responses and not a guarantee that the true effect lies inside the interval. An interval that excludes zero is consistent with a nonzero mean difference under the calculation used; an interval that includes zero leaves both a zero contrast and contrasts in either direction compatible with the data. Interpretation also depends on whether the calculation’s assumptions fit the design and whether the analysis was prespecified. Those details are not reported in the registry record.

The unadjusted p-value describes how unusual a test statistic at least as extreme as the observed one would be under a null hypothesis of no mean difference, assuming the calculation’s model and other assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The registry record does not report its own inferential analyses, so the p-values discussed for the comparisons are recalculated unadjusted results, not registry-reported test results.

What can dispersion tell us?

Standard deviations provide context for the variability of the changes. Greater dispersion means individual changes are less tightly clustered around the group mean. In small studies, variability can make estimates less precise, because the mean difference is informed by both the size of the contrast and the spread of the observations. A mean and standard deviation alone do not reveal the shape of the data, the presence of outliers, or whether the score distribution satisfies a particular model. Distributional checks are not reported in the registry record.

The record gives a standard deviation for each treatment entry and comparison calculations with pooled standard deviations. Pooling treats the groups as having a common variance for the calculation. Whether that assumption was checked or was used in the trial’s own analysis is not reported. In an intra-individual design, the relevant variability for a paired comparison is the variability of within-person differences; it cannot be recovered from separate group standard deviations without the correlation information. This is a reason to treat the recalculated comparisons as descriptive checks rather than as a substitute for the trial’s own analysis.

Why can over-dispersion matter?

As a general statistical point, over-dispersion occurs when observed variability is greater than a model assumes. If a method understates the actual variability, standard errors may be too small and confidence intervals too narrow; a test may then appear more decisive than warranted. The registry record does not report a model for the primary endpoint or diagnostics for variance assumptions. This general issue is a consideration when interpreting any model-based result, not a finding that over-dispersion occurred in this study.

Similarly, general principles about paired data matter because the record labels the primary population intra-individual. When treatment outcomes within a person are correlated, a method that recognizes that correlation can use the within-person comparison directly. Ignoring the pairing can misstate uncertainty in either direction, depending on the correlation. The registry record does not explain whether the official analysis used such a method, so no conclusion about the direction or magnitude of any impact is justified.

Finally, statistical significance and clinical importance are distinct. A mean difference may be estimated with an interval that excludes zero without meeting an unreported threshold of importance; conversely, an uncertain estimate does not prove absence of a meaningful effect. The registry record does not report a clinically important difference threshold for TCS. The appropriate reading is therefore to consider the direction and magnitude of the score changes, the interval estimates, the design and analysis uncertainties, and the restricted endpoint together.

11. Confidence Intervals and Precision

The confidence intervals quantify uncertainty in the recalculated mean differences, conditional on the calculations and assumptions used. They are not intervals for the range of participant-level changes. In the comparison of LEO 90100 with vehicle plus betamethasone, the interval is entirely below zero, which is compatible with a larger mean reduction in TCS for LEO 90100 under this subtraction order. The interval’s endpoints, -1.938 and -0.142, also show that the magnitude is not pinned down to a single value.

For the comparison with vehicle alone, the interval is entirely above zero; the positive contrast reflects the less negative mean change in that reference group. For the comparison with Daivobet® ointment, the interval spans values on both sides of zero. That range does not resolve the direction of the mean difference at the level represented by this calculation. It should not be interpreted as proof of no difference or as evidence of equivalence.

Precision is affected by the amount of variability and the information available in the comparison. The group standard deviations describe variability in the observed change scores, while the intervals describe uncertainty about the mean contrast. The record reports 24 in each primary-outcome group, but does not provide an interval from the trial’s own analysis or explain how intra-individual dependence was handled. The recalculated intervals therefore should not be confused with intervals from a reported paired or otherwise adjusted model.

Intervals also do not account for every uncertainty in interpretation. The registry record does not report a multiplicity adjustment, a clinically important TCS threshold, or the analysis plan. These omissions matter when considering how much weight to assign to one contrast among several. The intervals describe statistical precision for the calculations, not certainty about clinical relevance or generalizability.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect, not the trial’s original design assumptions. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The original sample-size justification and assumptions for the study itself are not reported in the registry record.

The 80% power column indicates the number of participants per arm that the planning calculation estimates would give an 80% chance of detecting the assumed effect under those assumptions, if that effect and model were correct. The 90% power column describes the corresponding planning target for a 90% chance. These are design illustrations, not guarantees about the outcome of a future study. The figures are not observed power and do not tell how likely the observed result was to be true.

The planning rows scale the effect being targeted relative to the observed contrast. Planning for 100% of the observed effect uses the full observed estimate; planning for 75% or 50% of the observed effect assumes a smaller effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm to reach the same target power. The resulting numbers can change substantially across effect assumptions, especially when the observed contrast is small or imprecise.

Because these calculations use effects observed in a small study and simplified assumptions, they should be treated as rough planning illustrations rather than recommendations. They do not account for an unreported paired design, multiplicity, attrition, or any analysis details not included in the stated planning assumptions. The registry record does not report the original rationale for enrollment.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -1.040; pooled standard deviation σ = 1.587.
2. n = 2 × (1.96 + 0.842)² × 1.587² / -1.040² = 36.5, rounded up to 37 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
delta <- -1.04                      # observed difference in means
sigma <- 1.58672618935971                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1347255)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 37 (80% power), 49 (90% power)
 75% of observed effect: n per arm = 65 (80% power), 87 (90% power)
 50% of observed effect: n per arm = 147 (80% power), 196 (90% power)
power.t.test: 37.5 
Simulated power at n = 37 per arm: 0.793 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple treatment comparisons and several outcomes, but it does not report a multiplicity plan. It is therefore not possible to determine whether the trial designated one comparison as primary for inference, used a testing hierarchy, adjusted p-values or confidence intervals, or treated secondary outcomes as exploratory. The recalculated p-values described in the interpretation are unadjusted and should be understood as individual comparisons, not as results corrected for the full set of comparisons.

As a general statistical point, when several hypotheses are tested, the chance of at least one apparently unusual result can rise if each test is considered separately. Adjustment procedures can address that issue, usually at a cost to precision or power. No procedure should be assumed for this study because the registry record does not report one. The unadjusted comparisons may be informative about the posted summaries, but they do not by themselves establish confirmatory evidence across all listed outcomes and treatments.

Missing-data handling is also not reported in the registry record. Although the primary outcome lists 24 for each treatment entry, the record does not say whether those are all randomized participants, all treated participants, or the number with endpoint data; nor does it describe withdrawals, missing observations, imputation, or exclusions. The listed numbers alone cannot establish that every participant contributed a complete observation or that missingness had no effect.

The primary population is described as intra-individual, but eligibility for that population and the handling of incomplete within-person measurements are not reported. Details of the statistical analysis plan, model, covariate adjustment and treatment of protocol deviations are also not reported in the registry record. These omissions limit assessment of whether the recalculated summaries reproduce the intended analysis and how robust the inference is to analytic choices.

The registry lists no reported analyses. Thus the recalculations should not be mistaken for the sponsor’s prespecified inferential analysis. Without a reported plan, the distinction between confirmatory and exploratory questions cannot be reconstructed from the outcome results alone.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent non-serious adverse event terms

For the LEO 90100 cutaneous spray, ointment group, 0 serious adverse events affected among 24 at risk. The registry entries also report 10 other adverse events affected among 24 at risk. These are counts of affected participants as recorded, not estimates of comparative risk. The safety details include only this treatment group, so they do not support a comparison with the vehicle groups or Daivobet® ointment.

The serious adverse event terms are not reported in the registry record. Deaths are not reported in the registry record; a missing death count should not be interpreted as confirmation that there were no deaths. The registry record does not provide definitions, event timing, severity details for other adverse events, reasons for discontinuation, or a fuller safety analysis. The figures therefore provide a limited description of the posted safety information, not a complete assessment of safety.

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

The primary results describe average changes in a clinical sign score over the study period. The mean change was more negative for LEO 90100 than for the vehicle with betamethasone, and the recalculated unadjusted contrast has a confidence interval entirely below zero. The comparison with vehicle alone also points to a larger mean score reduction for LEO 90100. These estimates are useful descriptions of the posted plaque-test results, but interpretation depends on the design and analysis assumptions that are not fully documented in the registry record.

The comparison with Daivobet® has an interval spanning zero. That does not demonstrate that the treatments are the same, nor does it rule out a difference in either direction. Establishing equivalence or non-inferiority would require a suitable prespecified margin and an analysis designed for that purpose; those details are not reported in the registry record.

The findings do not establish that LEO 90100 is effective or ineffective in general clinical use. The endpoint is a change in TCS from baseline to Day 29 in a psoriasis plaque test, not a measure of long-term control, recurrence, quality of life, or every relevant clinical outcome. The registry record does not report a threshold for a clinically important TCS change, so statistical contrasts cannot be translated into a claim about clinical importance.

The study is described as randomized and single-masked, yet also as a single-group study with an intra-individual analysis population. The record does not explain the relationship among these descriptions or how within-person comparisons were analyzed. In addition, the registry lists no reported analyses, and multiplicity and missing-data procedures are not reported. Those limits argue for reading the contrasts as summary-based recalculations rather than as a complete account of the trial’s confirmatory evidence.

More broadly, the data support a statement about the posted means and their calculated uncertainty in this study. They do not establish durability, generalizability to other populations or settings, or a benefit-harm balance across treatment groups. Safety information is limited to the reported LEO 90100 group, so comparative safety cannot be inferred from these figures.

17. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison cannot be interpreted from the direction of a mean alone. The TCS changes are negative across the listed primary-outcome groups, so the comparison depends on how much each group’s score changed, not simply on whether its score decreased. Reporting the contrast alongside the group means and its interval makes the direction and uncertainty easier to understand.

It also highlights the importance of matching the statistical method to the design. The registry labels the primary population intra-individual, a description that raises the possibility of correlated observations, while the record does not explain how the analysis handled that structure. Recalculations from group summaries can be useful checks, but they may not reproduce a paired or otherwise design-aware analysis.

The study provides a useful example of the distinction between an observed effect and a planning target. Sample-size illustrations based on observed contrasts can vary markedly depending on the assumed effect size. They do not reveal whether the original study was adequately planned, because the original design assumptions are not reported, and they are not evidence of observed power.

Finally, the registry record has no reported analyses and does not describe multiplicity or missing-data procedures. A statistically notable unadjusted result is not automatically a confirmatory finding when the analysis plan and the role of multiple outcomes are unknown. These reporting details are central to deciding how far a result can support a scientific conclusion.

18. 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.

The registry record leaves important design details unresolved. It describes the study as randomized, single-masked and single-group, and calls the primary analysis population intra-individual, but does not explain treatment assignment, the unit of randomization, the role of each treatment entry, or how correlated observations were handled. This makes it difficult to determine how closely the summary-based recalculations match the intended analysis.

The record lists no reported analyses. It does not describe the statistical model, prespecified contrasts, multiplicity adjustment, missing-data procedures, analysis population rules or handling of protocol deviations. The primary endpoint is reported with group means and standard deviations, but no participant-level distributions or within-person covariance are available in the registry entries. Consequently, the recalculated comparisons cannot resolve potential dependence between observations.

There is no reported threshold for a clinically important TCS change, and the outcome is measured at Day 29. Longer-term results and broader patient-centered outcomes are not reported in the registry record. Numerical results are also absent for several listed secondary outcomes, limiting assessment of consistency across measures.

The safety information is limited to the LEO 90100 group. Serious event terms and deaths are not reported, and the record does not provide comparative safety data for the other treatment entries. Finally, planning illustrations use observed effects and specified simplified assumptions, while the original sample-size justification is not reported. These limitations constrain conclusions about precision, clinical importance, generalizability and comparative safety.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Psoriasis Plaque Test Study With LEO 90100 Cutaneous Spray, Ointment, in Psoriasis Vulgaris — NCT01347255.
• Registry record last updated 2025-03-07; status last verified 2016-07.
• Results first posted 2016-02-24.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

This completed phase 2 psoriasis plaque test study enrolled 24 and compared reported mean changes in TCS across LEO 90100 cutaneous spray, ointment, vehicle preparations and Daivobet® ointment. The primary endpoint was change from Day 1 to Day 29 on a 0-to-9 score summing erythema, scaling and infiltration.

The mean TCS change was -6.0 for LEO 90100. Recalculated unadjusted comparisons indicate a more negative mean change than with vehicle plus betamethasone and vehicle alone; the comparison with Daivobet® is less precise and its interval includes zero. These are summary-based recalculations, not reported registry analyses.

The registry record does not report the trial’s analysis plan, multiplicity or missing-data procedures, or how the intra-individual analysis population was handled. Secondary numerical results are limited, and safety information is reported only for the LEO 90100 group. The findings should therefore be read as short-term plaque-test score results with important analytic and reporting limitations.