LEO 90100 Compared With Calcipotriol Plus Betamethasone Dipropionate Ointment, LEO 90100 Vehicle and Ointment Vehicle in Subjects With Psoriasis Vulgaris: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for LEO 90100 Compared With Calcipotriol Plus Betamethasone Dipropionate Ointment, LEO 90100 Vehicle and Ointment Vehicle in Subjects With Psoriasis Vulgaris (NCT01536886), a randomized phase 2 study. The primary outcome is Subjects With 'Controlled Disease' ('Clear'/'Almost Clear' for Subjects w. at Least Moderate Disease at Baseline, 'Clear' for Subjects With Mild Disease at Baseline) According to the Investigator's Global Assessment (IGA) on the Trunk and Limbs at Week 4..

2. Clinical Question

The trial was randomized, triple masked and parallel, with four arms. Its stated purpose was to investigate whether LEO 90100 and calcipotriol plus betamethasone were effective in treating psoriasis vulgaris. The primary outcome is a short-term assessment of disease severity, not a measure of long-term disease control or outcomes beyond the specified body regions.

The clinical question therefore concerns both active treatments and their respective vehicles, but the available comparison estimates address each active arm or the ointment vehicle against the LEO 90100 vehicle. Those estimates do not, by themselves, establish the result of a direct comparison between the two active treatments. The registry record does not report a separate direct estimate for that question.

3. Trial Design

This completed phase 2 study was randomized, triple masked and used a parallel-group design. The registry record lists an enrollment of 376. It lists four arms: LEO 90100, calcipotriol plus betamethasone dipropionate ointment, LEO 90100 vehicle and ointment vehicle. The LEO 90100 foam and the active ointment contain the same stated amounts of calcipotriol and betamethasone, but are described in different formulations. Each vehicle is described as having no active ingredient.

The registry record gives a study start of 2012-05 and primary completion of 2012-09, and lists the study status as completed. The condition is psoriasis vulgaris, and the listed phase is phase 2. The sponsor is LEO Pharma. The record does not provide further details about how randomization was generated, how treatment allocation was concealed, or which parties were masked.

The primary outcome was assessed at week 4 by an investigator using a five-point scale: clear, almost clear, mild, moderate or severe. The scale description refers to plaque thickening, scaling and erythema and says that the assessment was based on disease condition at the time of evaluation. The outcome is reported as a count of participants meeting the defined controlled-disease criterion, rather than as a mean score or a change from baseline.

The posted outcome results list 141 participants in the LEO 90100 arm, 135 in the active ointment arm, 49 in the LEO 90100 vehicle arm and 51 in the ointment vehicle arm. Counts with controlled disease were 77, 58, 3 and 4, respectively. The registry record does not report the reason that the primary-outcome arm counts differ from the overall enrollment or give a participant flow account. It also does not report the trial’s original sample-size justification or detailed design assumptions.

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: Prior to random., the subjects entered a washout phase (if required) where antipsoriatic treatm. and other relevant medication/treatms. had to be discontinued as defined by the excl. criteria. Depending on prior use of disallowed treatms, the washout/screening phase could last for up to 4 w prior to the first admin. of investigational products.

Overall Study

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 Subjects With 'Controlled Disease' ('Clear'/'Almost Clear' for Subjects w. at Least Moderate Disease at Baseline, 'Clear' for Subjects With Mild Disease at Baseline) According to the Investigator's Global Assessment (IGA) on the Trunk and Limbs at Week 4., measured over 4 weeks.

The primary endpoint counts participants who met the trial’s definition of controlled disease at week 4, based on the investigator’s global assessment of the trunk and limbs. For those with at least moderate disease at baseline, controlled disease meant clear or almost clear. For those with mild disease at baseline, it meant clear. The measure is therefore a binary outcome: each participant either meets the specified criterion or does not.

The underlying assessment used a five-point severity scale ranging from clear to severe, with plaque thickening, scaling and erythema considered. A threshold on that scale makes the result easier to interpret as the number of participants attaining a defined disease state at the assessment visit. It also discards some detail: participants on opposite sides of the threshold are placed in different categories, while variation within either category is not conveyed by the endpoint count.

Using an investigator assessment allows the endpoint to reflect a clinical rating of disease appearance in the specified body regions. The registry record does not report additional information about assessment training, assessor consistency or procedures for handling an assessment that could not be completed. The endpoint concerns status at week 4; it does not, on its own, describe the time course of change, persistence of control after that visit, or outcomes outside the trunk and limbs.

The posted results give counts meeting the criterion by arm: 77 of 141 for LEO 90100, 58 of 135 for calcipotriol plus betamethasone ointment, 3 of 49 for LEO 90100 vehicle and 4 of 51 for ointment vehicle. These counts describe the posted endpoint results. They should be interpreted together with the comparison estimates and their uncertainty, rather than as complete measures of every aspect of psoriasis severity.

7. Results Posted in the Registry

• LEO 90100: 54.6% (77/141) versus 6.1% (3/49) on control; risk difference 48.5 percentage points (95% CI 37.9 to 59.1), risk ratio 8.92 (2.95–26.98); unadjusted two-proportion z-test p = <0.001.
• Calcipotriol Plus BDP Ointment: 43.0% (58/135) versus 6.1% (3/49) on control; risk difference 36.8 percentage points (95% CI 26.1 to 47.6), risk ratio 7.02 (2.30–21.37); unadjusted two-proportion z-test p = <0.001.
• Ointment Vehicle: 7.8% (4/51) versus 6.1% (3/49) on control; risk difference 1.7 percentage points (95% CI -8.3 to 11.7), risk ratio 1.28 (0.30–5.43); unadjusted two-proportion z-test p = 0.736.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary: the investigator’s assessment placed each participant on a five-point disease-severity scale, and a baseline-dependent threshold determined whether the participant counted as having controlled disease. For those with at least moderate disease at baseline, the qualifying states were clear or almost clear. For those with mild disease at baseline, the qualifying state was clear. The posted arm results are counts of participants who met this definition.

What does a risk difference describe?

A risk difference compares the proportion with the outcome in one arm with the proportion in another arm by subtraction. A positive value means that the outcome was more frequent in the first-named arm in the posted comparison; a negative value means it was less frequent. The reported estimates are 0.485 for LEO 90100 versus LEO 90100 vehicle, 0.368 for calcipotriol plus betamethasone ointment versus LEO 90100 vehicle, and 0.017 for ointment vehicle versus LEO 90100 vehicle. These are unadjusted comparisons. The registry record does not report a separate estimate directly comparing the two active treatments.

Risk differences keep the comparison on the absolute probability scale. This can make the size and direction of an observed difference more directly interpretable than a relative measure, but the value still depends on the population, outcome definition and comparator. The risk difference does not describe why the groups differed, and it does not capture outcomes other than the specified controlled-disease endpoint.

How should a confidence interval be read?

A confidence interval expresses the uncertainty around an estimated effect under the statistical method used to construct it. It indicates a range of effect values that are reasonably compatible with the observed data and the method’s assumptions. It is not a guarantee that the true effect lies in that particular interval, and it does not account for every possible problem in study conduct or outcome reporting.

The interval for LEO 90100 versus its vehicle runs from 0.379 to 0.591. The interval for the active ointment versus that vehicle runs from 0.261 to 0.475. The interval for ointment vehicle versus LEO 90100 vehicle runs from -0.083 to 0.117. The last interval includes zero, so the data are compatible with no risk difference as well as with differences in either direction under the interval’s assumptions. The registry record does not state the method used to construct these intervals.

What does the p-value add?

A p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, and it is not a measure of the size or clinical importance of an effect. The two active-treatment comparisons have unadjusted p < 0.001; the ointment-vehicle comparison has p = 0.736. These values do not replace the effect estimates and confidence intervals, and the p-values are not reported as adjusted for multiple comparisons.

Because multiple comparisons are listed, interpretation of each p-value depends on the analysis context. The registry record does not report whether comparisons were prespecified in a statistical plan, whether any multiplicity adjustment was intended, or how the analyses were selected. It would therefore be inappropriate to infer a confirmatory testing strategy from the posted p-values alone.

Why can over-dispersion matter in other outcome models?

General statistical explanation: over-dispersion arises when data vary more than a model assumes. If that extra variation is ignored, standard errors can be too small and confidence intervals too narrow, making results appear more precise than warranted. This trial’s primary outcome is a binary count, and the registry record does not describe a model that requires an over-dispersion adjustment. The concern is relevant when choosing methods for other kinds of outcomes, but it should not be attributed to this analysis without evidence.

The posted summary does not report the statistical test or interval-construction procedure. The risk-difference estimates and their intervals can be described as posted, but no specific method should be inferred from their format. The registry record also does not report adjustments for baseline covariates, stratification factors or clustering. It is therefore not possible to determine from the record whether the estimates are crude in every respect beyond their identification as unadjusted comparisons.

10. Confidence Intervals and Precision

The confidence intervals convey how precisely the risk differences are estimated in the posted comparisons. For LEO 90100 versus the LEO 90100 vehicle, the estimate is 0.485 and the interval extends from 0.379 to 0.591. For calcipotriol plus betamethasone ointment versus the same vehicle, the estimate is 0.368 and the interval extends from 0.261 to 0.475. Both intervals lie above zero. This indicates that, under the interval method’s assumptions, the data are compatible with positive risk differences across the reported ranges.

The ointment-vehicle comparison has an estimate of 0.017 and an interval from -0.083 to 0.117. This interval spans zero and includes both negative and positive risk differences. Its breadth relative to the estimate means the posted data do not pin down the direction or size of a difference between the vehicles with comparable precision to the two active-treatment comparisons.

A confidence interval’s width reflects statistical uncertainty, but it does not describe all uncertainty. It cannot account for unreported missing-data decisions, departures from the analysis plan, measurement issues or other risks of bias. The registry record does not report the interval method or analysis population, so precision should be interpreted as conditional on methods and data handling that are not fully described.

The arm sizes differ, and the vehicle arms have fewer participants than the active-treatment arms. The posted arm counts are relevant context for interpreting uncertainty, but the registry record does not supply enough information to reconstruct the analysis. Avoid treating the number of decimal places in an estimate as evidence of high precision: the confidence interval is the more informative indication of statistical uncertainty. No interval for a direct active-treatment comparison is reported.

11. 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 illustrations for a future study based on fractions of the observed risk difference, not the trial’s original design. For these comparisons, the entries 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. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% probability of detecting the selected effect under the stated assumptions, if that effect is the true one and the model assumptions hold. The 90% power column gives the corresponding planning figure for a 90% probability. These are design probabilities, not probabilities that a result is true. This is not observed power.

Rows describe planning for the full observed effect, 75% of the observed effect and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so planning for a smaller effect requires more participants per arm under the same assumptions. The values vary substantially by comparison, especially where the observed risk difference is close to zero; small observed effects can yield very large planning illustrations when the goal is to detect a fraction of them.

The figures are not predictions of what a future trial will achieve. They do not account for unreported choices such as expected loss to follow-up or a different analysis method. A reader should select the comparison and effect fraction relevant to a future research question, then treat the listed figures as conditional illustrations rather than a substitute for a full design calculation.

12. 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 = 0.061; treatment proportion p₁ = 0.546; average p̄ = 0.304.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6503 = 1.2746.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5526 = 0.4651.
4. n = (1.2746 + 0.4651)² / (0.4849)² = 12.9, rounded up to 13 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 <- 0.0612244897959184                          # control proportion
p1 <- 0.546099290780142                          # 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(1536886)
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 = 13 (80% power), 17 (90% power)
 75% of observed effect: n per arm = 21 (80% power), 28 (90% power)
 50% of observed effect: n per arm = 39 (80% power), 52 (90% power)
power.prop.test: 12.9 
Simulated power at n = 13 per arm: 0.845 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome measure and no posted secondary outcome results. It lists no analyses in the analysis count, although primary comparison estimates are posted. The record does not report a statistical analysis plan describing which comparisons were planned, how outcomes were prioritized, or whether analyses were conducted before or after the data were examined.

Multiplicity arises when several hypotheses or outcomes are tested. With repeated testing, the chance of obtaining at least one apparently unusual result can increase. Statistical plans may address this through a testing hierarchy, adjustment of significance thresholds, or other approaches. The registry record does not report whether any such procedure was planned or used. The displayed p-values are unadjusted, so they should not be treated as if a multiplicity correction had been applied.

Missing-data handling is also not reported in the registry record. The posted primary endpoint counts have arm-specific denominators, but the record does not explain whether those denominators include every randomized participant, whether any outcome assessments were missing, or how missing outcomes were handled. It does not describe imputation, sensitivity analyses or reasons for missingness. Without these details, readers cannot assess how much the results might depend on the treatment of incomplete observations.

The analysis populations are not reported in the registry record. It is not stated whether the posted endpoint results use all randomized participants, participants who received treatment, or another defined population. The record also does not explain departures from assigned treatment, exclusions after randomization or adherence to the intended analysis. These details matter because different analysis populations can produce different estimates and may affect the benefits of randomization.

The registry record does not report interim analyses, stopping rules, or whether the primary outcome and its analysis were prespecified in a protocol or statistical plan. Those details should not be inferred from the phase, design or posted results. The absence of this information limits evaluation of the inferential framework, but does not change the descriptive arm counts and comparison estimates that are posted.

14. 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 serious adverse event terms

Serious events with the highest arm-level rate: bile duct stone (0.7%), bronchitis (0.7%), hypertension (0.7%).

The serious adverse event figures report one event among 134 participants at risk in the calcipotriol plus betamethasone ointment arm. The registry lists zero serious adverse events among 141 at risk in the LEO 90100 arm, 49 at risk in the LEO 90100 vehicle arm, and 51 at risk in the ointment vehicle arm. The arm-specific risk counts are the denominators for reading these safety entries; they are not identical to every primary-outcome denominator.

The registry record lists bile duct stone, bronchitis and hypertension among the top serious-event terms, each at 0.7%. It does not identify which arm or arms account for each listed term, so those terms should not be assigned to a treatment group. Deaths are not reported in the registry record.

These are safety counts for the recorded period and event definitions, not comprehensive measures of all possible harms. The record does not report event onset, duration, severity beyond the serious classification, relationship to treatment, or a detailed collection period. A zero in a posted count means no event was recorded for that category in that arm; it does not establish that an event is impossible or that the treatment has no safety risk.

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

The posted primary results show that more participants met the controlled-disease criterion in each active-treatment arm than in the LEO 90100 vehicle arm at week 4. The risk-difference estimates are positive for both active comparisons, with confidence intervals above zero and unadjusted p < 0.001. The ointment-vehicle estimate is much closer to zero, and its confidence interval includes zero. These statements describe the short-term endpoint and the comparisons reported in the registry record.

They do not establish the relative effect of LEO 90100 compared directly with calcipotriol plus betamethasone ointment. Both active-treatment estimates use the LEO 90100 vehicle as comparator, and the record does not post a direct active-versus-active estimate. Nor do the results establish that the two vehicles are equivalent: the vehicle comparison has uncertainty extending in both directions.

The endpoint is a thresholded investigator assessment of the trunk and limbs at week 4. It does not show whether an improvement persisted, how disease changed at other times, or what happened on other body regions. The registry record does not report secondary outcomes, longer-term results, patient-reported outcomes or details of missing data and analysis populations. It is not possible to use the posted primary outcome alone to answer those questions.

Randomization is a design feature intended to support fair comparisons, but the registry record does not give enough operational detail to evaluate random sequence generation, allocation concealment, masking implementation or all aspects of follow-up. Statistical estimates also remain subject to uncertainty, as the confidence intervals demonstrate. A small p-value does not measure clinical importance, eliminate bias or prove that a result will apply in other settings.

The safety entries are similarly limited: they describe the reported serious-event counts and do not provide a complete evaluation of adverse effects. Overall, the findings are evidence about the listed arms, endpoint and time point in this completed phase 2 trial. They should not be extended beyond those boundaries or interpreted as medical advice.

16. Why This Trial Matters Statistically

This trial is statistically useful because it includes two active formulations and two corresponding vehicle controls, while reporting a binary investigator-assessed endpoint. That structure allows the posted results to distinguish the active-treatment comparisons with the LEO 90100 vehicle from the vehicle comparison itself. It also illustrates why the comparator used for an estimate must be stated explicitly: an effect estimate against a vehicle does not answer a direct comparison between active treatments.

The results demonstrate the value of considering effect estimates and confidence intervals together. The two active-treatment risk differences are positive and their reported intervals remain above zero, whereas the ointment-vehicle estimate is close to zero and its interval spans zero. The p-values alone would not communicate the size or uncertainty of these effects. Conversely, the point estimate alone would not show how much uncertainty surrounds it.

The trial also highlights interpretation challenges in short-term threshold outcomes. A binary controlled-disease measure is easy to express as a count, but it compresses a five-point severity assessment into a yes-or-no classification. Different baseline thresholds are used for mild disease and at least moderate disease. The record does not give subgroup counts, so the overall endpoint cannot show how results vary by baseline severity.

Finally, the record makes clear that posted results and full statistical documentation are not the same thing. Details on missing data, analysis populations, multiplicity and original sample-size planning are not reported. Those omissions constrain assessment of the analysis without changing the reported arm-level counts. For biostatisticians and clinical researchers, the key lesson is to keep the design, endpoint, comparator, estimate, uncertainty and reporting gaps distinct when interpreting a clinical trial.

17. 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 provides limited information for evaluating trial conduct beyond stating that the study was randomized, triple masked and parallel. It does not report the randomization method, allocation concealment procedures, masking details or the practical steps used to maintain masking. These omissions prevent a fuller assessment of potential selection and measurement biases.

The primary endpoint is assessed at week 4 and is restricted to the trunk and limbs. The record does not report later assessments, durability of the controlled-disease state, or additional outcomes that could provide a broader account of disease severity. The threshold-based definition also does not preserve the full information in the five-point scale. No results by baseline severity are posted, despite the endpoint’s different threshold for mild versus at least moderate baseline disease.

The record does not explain why the primary-outcome denominators vary by arm or how missing assessments were handled. It does not report analysis populations, adherence, participant flow or sensitivity analyses. The safety at-risk count for the active ointment arm is 134, while its primary-outcome arm count is 135; the registry record does not explain this difference. No reason should be inferred from the counts alone.

There are no posted secondary outcome results, and details of multiplicity control, prespecification, interim analyses and the original sample-size justification are not reported in the registry record. The posted comparisons are unadjusted and do not include a direct comparison between the active treatments. These limitations restrict interpretation to the specified short-term endpoint and reported comparisons, rather than a complete assessment of the trial’s broader clinical or statistical questions.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: LEO 90100 Compared With Calcipotriol Plus Betamethasone Dipropionate Ointment, LEO 90100 Vehicle and Ointment Vehicle in Subjects With Psoriasis Vulgaris — NCT01536886.
• Registry record last updated 2025-03-07; status last verified 2016-08.
• Results first posted 2015-12-09.
• 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.

21. Record Summary

NCT01536886 is a completed randomized, triple-masked, parallel phase 2 study sponsored by LEO Pharma. The registry record lists psoriasis vulgaris as the condition, enrollment of 376, a study start of 2012-05 and primary completion of 2012-09. Four arms were listed: LEO 90100 aerosol foam, calcipotriol plus betamethasone dipropionate ointment, LEO 90100 vehicle and ointment vehicle.

The primary outcome was the number of participants with investigator-assessed controlled disease on the trunk and limbs at week 4. The posted counts were 77 of 141 for LEO 90100, 58 of 135 for the active ointment, 3 of 49 for LEO 90100 vehicle and 4 of 51 for ointment vehicle. Unadjusted risk differences are reported for each listed arm against LEO 90100 vehicle. A direct active-treatment comparison is not reported.

The record does not report secondary outcome results, a detailed statistical analysis plan, missing-data procedures or analysis populations. Serious adverse event counts and terms are listed, but deaths are not reported in the registry record.