Subject Preference for Scalp Psoriasis Treatment: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Subject Preference for Scalp Psoriasis Treatment (NCT00438399), a randomized phase 3 study. The primary outcome is Percentage of Subjects Preffering Clobetasol Propionate Shampoo Better Than Comparator.

2. Clinical Question

3. Trial Design

This was a completed phase 3, randomized, single-masked crossover trial. Enrollment was 219. In a crossover design, participants receive treatments in a sequence rather than being assigned to only one treatment throughout the study. The registry lists sequences in which clobetasol propionate shampoo was given before or after each of the three comparators, with a washout period between treatments. The washout is described as up to 8 weeks, and the shampoo treatment period as a maximum of 4 weeks.

The design sought to compare preference for the shampoo with preference for each comparator. Each comparator therefore forms a separate comparison with the shampoo. The registry does not identify who was masked, describe how masking was maintained, or give complete treatment details for all comparator periods. It also does not report period-specific participant counts or explain how treatment sequence, period, or possible carryover effects were handled in the analysis.

The primary endpoint is described as being assessed at the end of Period II, up to 16 weeks, in the intention-to-treat population. The endpoint description names a nonparametric, two-sided Wilcoxon rank signed test. The posted analysis entries instead label the method Wilcoxon (Mann-Whitney). The record does not reconcile these method descriptions. It also does not report the original design assumptions, a sample-size justification, or details of interim analyses.

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: 219 participants recruited.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to Treat population (ITT).

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 Subjects Preffering Clobetasol Propionate Shampoo Better Than Comparator, measured over End of period II (up to 16 weeks).

The primary endpoint is the percentage of participants whose overall preference favored clobetasol propionate shampoo over a comparator at the end of Period II, up to 16 weeks. The registry describes preference responses as including the shampoo being a lot better or a little better, and the comparator being a lot better or a little better. It does not provide the full response distribution, explain how ties or other responses were treated, or report an endpoint value for every preference category.

Preference is relevant to a comparison of topical treatments because the registry’s study rationale describes practical aspects of topical therapy, including inconvenience, messiness, and possible effects on hair. A preference endpoint can capture participants’ overall assessments of treatment experience. It answers a different question from an endpoint measuring clinical signs or symptoms: a preference result alone does not establish how much psoriasis changed or whether one treatment was clinically more effective.

The endpoint is reported separately for the shampoo compared with each of three corticosteroids. The registry identifies the intention-to-treat population and specifies a nonparametric test in the endpoint description. However, the posted percentages do not show all response categories or the underlying ordinal data. Consequently, the percentages alone cannot reproduce the stated rank-based analysis or clarify exactly how the preference responses contributed to it.

7. Results Posted in the Registry

• C. Propionate Compared to Corticosteroid 2: 31.7% (19/60) versus 28.6% (18/63) on control; risk difference 3.1 percentage points (95% CI -13.1 to 19.3), risk ratio 1.11 (0.65–1.90); unadjusted two-proportion z-test p = 0.708.
• C. Propionate Compared to Corticosteroid 3: 21.8% (12/55) versus 28.6% (18/63) on control; risk difference -6.8 percentage points (95% CI -22.4 to 8.9), risk ratio 0.76 (0.40–1.44); unadjusted two-proportion z-test p = 0.401.

8. Statistical Interpretation

9. Statistical Methods Explained

For the primary endpoint, the registry describes preference as an ordered response: the shampoo could be judged a lot better or a little better, and the comparator could be judged a lot better or a little better. The endpoint description specifies a two-sided nonparametric Wilcoxon rank signed test in the intention-to-treat population. In general, a rank-based test uses the ordering of observations rather than assuming that the outcome follows a particular continuous distribution. A two-sided test evaluates evidence of a difference in either direction, rather than prespecifying only one direction.

Why the test descriptions matter

The endpoint description names a Wilcoxon rank signed test, while the posted analysis entries label the method Wilcoxon (Mann-Whitney). In general, the signed-rank test is used for paired or matched observations, while the Mann-Whitney rank-sum test is generally used to compare independent groups. Crossover designs commonly produce paired treatment observations, because a participant may receive more than one treatment. The registry does not explain how the posted test labels relate to the crossover data or why the two method descriptions differ. It would therefore be inappropriate to assume a particular implementation or to claim that the posted analysis accounted for pairing, sequence, period, or carryover.

The posted group percentages can also be compared using a binary risk difference. In general, a risk difference is the difference between the proportions with the specified outcome in two groups; zero represents equal proportions. The recalculated risk differences are simple unadjusted recalculations from the posted summary statistics. They are not a reproduction of the sponsor’s rank-based analysis, and they do not make use of the full ordered preference responses described in the endpoint.

How to read a p-value

In general, a p-value measures how incompatible 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, nor does it measure the size or importance of an effect. The sponsor’s reported p-values are attached to its comparator-specific analyses. Because the registry does not provide the sponsor’s effect estimates, full preference distributions, or enough details about the analysis, the magnitude and exact interpretation of those results cannot be reconstructed from the p-values alone.

The recalculated p-values of 0.708 and 0.401 arise from simple binary comparisons and are associated with their recalculated risk differences and intervals. They should not be read as replacements for the sponsor’s analysis. The registry’s discrepancy flag indicates a conflict between the posted summaries and recalculations, and the sponsor’s own analysis takes precedence.

Why crossover structure is relevant

In general, a crossover analysis can account for the fact that treatment responses from the same participant may be related. A paired analysis can use within-participant contrasts, while a suitable model may also address period or sequence effects. Those approaches can differ from treating summary percentages as if they came from independent groups. The registry does not report the full crossover analysis specification or enough participant-level information to reproduce one. The simple recalculations should therefore be interpreted as limited summaries, not as a substitute for a complete analysis of the trial design.

The registry identifies the primary analysis population as intention to treat. In general, an intention-to-treat analysis aims to analyze participants according to their randomized assignment, but the registry record does not give the detailed rules used for this endpoint, including how incomplete treatment periods or missing preference responses were handled. It also does not state whether the sponsor used an adjustment for the multiple comparator tests. No secondary outcome results are posted in the record.

10. Confidence Intervals and Precision

The recalculated interval for the comparison of Corticosteroid 2 with Corticosteroid 1 runs from -0.131 to 0.193 around a risk difference of 0.031. The interval for Corticosteroid 3 compared with Corticosteroid 1 runs from -0.224 to 0.088 around a risk difference of -0.068. Both intervals include zero, which is the value corresponding to no difference in the binary proportions under this measure.

In general, a confidence interval describes a range of effect estimates compatible with the data and the method used. These intervals extend to values on either side of zero, so the recalculated summaries do not pin down the direction or size of either difference with precision. The registry does not report a confidence level for these recalculated intervals. The sponsor analysis entries specify 95% confidence intervals, but list no interval endpoints or effect estimates. Those entries therefore do not allow the sponsor’s precision to be assessed from the registry record.

Precision is also limited by the information available in the posted summaries. The full ordered preference responses, participant-level paired data, and complete crossover analysis are not reported in the registry record. Without those details, the simple intervals cannot represent all the information that may have been used in the sponsor’s analysis. They describe the recalculated binary comparisons only and should not be taken as intervals for the sponsor’s rank-based results.

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 estimates are stated as participants per arm, not total events. They are illustrations based on the observed effect, rather than the original design justification for this trial. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effects considered are 100%, 75%, and 50% of the observed effect.

The 80% power column gives the estimated participants per arm for a future comparison to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the other assumptions apply. The 90% power column gives the corresponding estimate for a 90% chance. These are planning targets, not counts of participants observed in the trial. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

Smaller effects require more participants in these illustrations: detecting a smaller fraction of the observed effect requires a larger planned sample per arm. The estimates differ between the two recalculated comparisons because their observed effects differ. This is not observed power; it is a forward-looking planning illustration based on the observed effect and stated assumptions. In general, a curve relating effect size to sample size expresses the same relationship: as the effect one aims to detect becomes smaller, the required sample grows under otherwise unchanged assumptions.

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 = 0.286; treatment proportion p₁ = 0.317; average p̄ = 0.301.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6488 = 1.2716.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6484 = 0.5457.
4. n = (1.2716 + 0.5457)² / (0.0310)² = 3,447.5, rounded up to 3,448 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 <- 0.285714285714286                          # control proportion
p1 <- 0.316666666666667                          # 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(438399)
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 = 3,448 (80% power), 4,615 (90% power)
 75% of observed effect: n per arm = 6,085 (80% power), 8,145 (90% power)
 50% of observed effect: n per arm = 13,588 (80% power), 18,190 (90% power)
power.prop.test: 3447.5 
Simulated power at n = 3,448 per arm: 0.800 (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. Analyses Reported by the Sponsor

The registry reports sponsor analyses using the label Wilcoxon (Mann-Whitney), with p < 0.001 for the Corticosteroid 1 comparison, p = 0.007 for the Corticosteroid 2 comparison, and p < 0.001 for the Corticosteroid 3 comparison. It does not include sponsor effect estimates, interval endpoints, or enough detail to reconstruct these tests from the posted preference percentages.

The simple recalculations compare the binary percentages for Corticosteroid 2 and Corticosteroid 3 against Corticosteroid 1. Their risk differences are 0.031 and -0.068, with p-values of 0.708 and 0.401. They are not recalculations of the sponsor’s rank-based analyses and do not cover the same reported set of contrasts. The registry flags a discrepancy, so the sponsor’s own analysis takes precedence. The recalculations are useful as a check on the posted binary summaries, but should not be substituted for the sponsor’s analysis or treated as a resolution of the discrepancy.

14. Multiplicity, Missing Data and Analysis Populations

The study objective involves comparing the shampoo with each of three topical corticosteroids. When several comparisons are tested, the chance of at least one false-positive result can increase if no adjustment or other multiplicity strategy is used. The registry record does not report whether the sponsor adjusted for multiple comparisons, used a prespecified testing sequence, or applied another strategy to address multiplicity. The sponsor’s reported p-values should therefore be read as posted, without assuming an adjustment that is not described.

The primary endpoint description identifies the intention-to-treat population. It does not provide participant counts for that analysis by comparator, nor does it describe how participants with incomplete crossover periods were handled. Missing preference responses, withdrawals, exclusions, and imputation methods are not reported in the registry record. The record also does not state whether the analysis included all randomized participants for each comparison or how the intention-to-treat principle was applied to the crossover sequence.

The registry reports no secondary outcome results. It does not provide an analysis plan or explain whether there were additional prespecified analyses. The endpoint description specifies a Wilcoxon rank signed test, whereas the posted analysis entries label the method Wilcoxon (Mann-Whitney). The record does not reconcile these descriptions or specify how the analysis addressed the paired nature of crossover data, period, sequence, or carryover. These omissions limit assessment of both the analysis population and the statistical methods. They do not establish that the methods were inappropriate; they mean the registry record does not give enough detail to evaluate those aspects fully.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cholecystolithiasis (1.5%), hospitalisation due to nausea (1.5%), hospitalization due to malaise (1.5%), allergic reaction (1.5%), unclear abdominal pain - mechanical subileus (0.5%).

The registry reports serious adverse events affecting 0 of 72 participants in the Corticosteroid 1 group, 2 of 67 in the Corticosteroid 2 group, 1 of 65 in the Corticosteroid 3 group, and 3 of 199 in the clobetasol propionate shampoo group. These are reported counts and at-risk group sizes. The registry does not explain how crossover exposure was handled for these safety groups, so the figures should be read as recorded rather than assumed to represent a particular exposure-adjusted analysis.

The serious-event terms listed include cholecystolithiasis, hospitalisation due to nausea, hospitalization due to malaise, and allergic reaction, each reported as 1.5%; unclear abdominal pain - mechanical subileus and angina pectoris, each reported as 0.5%. The record does not specify the relationship of each event to treatment in these entries. Death counts are not reported in the registry record. These adverse-event summaries are descriptive; the registry does not provide a statistical comparison of serious-event risk between treatments.

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

The posted outcome is a treatment-preference measure, not a direct estimate of change in scalp psoriasis. The recorded percentages show the proportion classified as preferring clobetasol propionate shampoo better than each comparator: 28.5% against Corticosteroid 1, 31.6% against Corticosteroid 2, and 21.8% against Corticosteroid 3. The registry also posts sponsor p-values for the comparator-specific analyses. Those p-values do not describe the size of a preference difference, and the record lacks sponsor effect estimates and full preference distributions.

The simple recalculations for Corticosteroid 2 and Corticosteroid 3 versus Corticosteroid 1 produce intervals that include zero. Because these recalculations use the posted binary summaries rather than the full ordered preference information, they do not resolve the sponsor results. The registry flags a discrepancy; the sponsor’s own analysis takes precedence. The record’s differing descriptions of the Wilcoxon method and lack of detail on the crossover analysis further constrain interpretation.

A preference result can reflect participants’ overall experience of treatment, which is relevant to practical use of topical therapies. It cannot, by itself, establish comparative clinical efficacy, durability, safety, or the degree of improvement in psoriasis. The registry record does not report results for a clinical-sign endpoint or provide enough information to assess how missing responses affected the preference analysis. The serious adverse-event counts are descriptive and are not a basis for inferring treatment causation or comparative safety.

Accordingly, the posted record documents preference analyses and adverse-event counts, but the scope of conclusions is limited by the endpoint’s nature, the discrepancy between the simple recalculations and sponsor results, and the missing analysis details. It does not support a broader claim about treatment benefit beyond the particular preference analyses reported.

17. Why This Trial Matters Statistically

This trial illustrates that the statistical result depends on how the outcome is represented and analyzed. The endpoint is described as an ordered preference response, and the planned method is rank-based. The posted arm-level percentages, by contrast, reduce the information to a binary indicator of whether the shampoo was preferred as better. Simple recalculations using those percentages do not reproduce the sponsor’s reported p-values. The distinction is important: a test using ordered responses can address a different feature of the data than a comparison of binary proportions.

The crossover structure is another statistical consideration. Participants can contribute experience with more than one treatment, so observations may be paired. In general, accounting for that structure can affect uncertainty and the test being used. The registry’s endpoint description and analysis labels do not fully explain how pairing or other crossover features were handled. This makes it difficult to independently assess the reported analysis from the registry summaries.

Finally, the study asks about preference, a meaningful but distinct outcome from clinical response. Preference can capture treatment experience, while it does not substitute for measures of disease severity or change. The record’s incomplete reporting of the response distribution, sponsor effect estimates, multiplicity strategy, and missing-data handling shows why statistical interpretation needs both effect estimates and a clear account of the analysis—not p-values alone.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not provide the full ordered preference distribution, sponsor effect estimates, or sponsor confidence-interval endpoints. The posted percentages therefore offer only a partial view of the primary outcome and do not permit reconstruction of the reported rank-based analyses. A discrepancy is flagged between the sponsor results and simple recalculations from the binary summaries.

There is also an unresolved difference between the endpoint description’s Wilcoxon rank signed test and the posted analysis label Wilcoxon (Mann-Whitney). The record does not describe whether the crossover pairing, treatment sequence, period, or carryover was handled in the analysis. Full details of the comparator drugs and their treatment regimens are not reported in the registry record, and the comparator descriptions are incomplete.

The record does not describe missing preference responses, withdrawals, exclusions, or imputation; it does not report an adjustment for the three comparator tests or the original sample-size justification. It identifies an intention-to-treat population but does not give participant counts for that primary analysis by comparator. No secondary outcome results are posted. Safety summaries give serious-event counts, but do not establish treatment attribution or present a statistical comparison. These gaps limit independent assessment of the analysis and the breadth of conclusions that can be drawn from the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Subject Preference for Scalp Psoriasis Treatment — NCT00438399.
• Registry record last updated 2021-02-18; status last verified 2011-11.
• Results first posted 2011-12-23.
• 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

The registry records a completed phase 3 randomized, single-masked crossover trial comparing clobetasol propionate shampoo 0.05% with three topical corticosteroids for moderate to severe scalp psoriasis. Enrollment was 219. The primary endpoint was participant preference at the end of Period II, up to 16 weeks, with the intention-to-treat population identified in the endpoint description.

Posted preference percentages favoring shampoo were 28.5% against Corticosteroid 1, 31.6% against Corticosteroid 2, and 21.8% against Corticosteroid 3. Sponsor analyses report p < 0.001, p = 0.007, and p < 0.001, respectively. Simple recalculations for two binary comparisons differ; the registry flags a discrepancy, and the sponsor’s own analysis takes precedence. Full effect estimates and analysis details are not reported in the registry record.