A Comparison of DFD01 Spray Versus Comp01 Lotion, Vehicle Spray and Vehicle Lotion in Subjects With Moderate Psoriasis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Comparison of DFD01 Spray Versus Comp01 Lotion, Vehicle Spray and Vehicle Lotion in Subjects With Moderate Psoriasis (NCT01947491), a randomized phase 3 study. The primary outcome is Percentage of Participants With Success According to the Investigator Global Assessment (IGA).

2. Clinical Question

3. Trial Design

The registry record describes a randomized, double-masked, parallel-group Phase 3 trial in participants with psoriasis. The trial status is completed, and enrollment is listed as 394. The record gives a start of 2013-11 and primary completion of 2015-01. These dates and enrollment describe the trial record, but do not establish how participants were distributed across all four intervention groups or which analysis populations were used for every outcome.

Four interventions are listed: DFD01 Spray, Vehicle Spray, Comp01 Lotion, and Vehicle Lotion. DFD01 Spray and Vehicle Spray were each used twice daily for 28 days. Vehicle Lotion was also used twice daily for 28 days, while Comp01 Lotion was used twice daily for 14 days. The primary efficacy endpoint is recorded at Day 15. The registry’s description says efficacy was only done on DFD01 Spray and Vehicle Spray, and specifically says no efficacy would be done on the comparator or its vehicle. Consequently, the posted primary efficacy comparison is not a four-group comparison.

The efficacy outcome lists 174 participants for DFD01 Spray and 87 for Vehicle Spray. The Comp01 Lotion and Vehicle Lotion rows have no primary endpoint participant counts or outcome values; those entries do not provide efficacy results for those groups. The safety record lists separate at-risk counts for all four interventions. Those safety counts should not be treated as the denominators for the primary efficacy result.

The registry record does not report the randomization ratio, how randomization was implemented, the masking procedures, or the original sample-size justification. It also does not describe stratification, center effects, or other design features beyond randomized allocation, double masking, and a parallel model. Such details should not be inferred from the posted group sizes or analysis result.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Efficacy was only done on DFD01 Spray and Vehicle Spray. Protocol specifically noted no efficacy would be done on comparator or its vehicle.

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 Success According to the Investigator Global Assessment (IGA), measured over Day 15.

The primary endpoint is the percentage of participants with success according to the Investigator Global Assessment (IGA) at Day 15. Success is defined in the registry record as an IGA assessment of clear or almost clear. This is a binary outcome: a participant is classified according to whether the stated assessment threshold was met. The measure therefore reports the share of participants reaching that category, rather than the average of a continuous severity score or the amount of change from baseline.

An investigator global assessment is used to describe an overall clinical status on an assessment scale. A threshold such as clear or almost clear turns that assessment into a readily interpretable success proportion. The usefulness of a binary endpoint depends on the definition being applied consistently and on how participants with missing or unevaluable assessments are handled. The registry record does not describe the assessment process in further detail or explain how missing Day 15 assessments were treated.

The posted primary endpoint reports 19.0% for DFD01 Spray, with a 95% confidence interval from 13.1% to 24.8%, and 2.3% for Vehicle Spray, with a 95% confidence interval from 0.0% to 5.4%. These values are for the spray comparison only. The registry record states that efficacy was not done for Comp01 Lotion or Vehicle Lotion. Thus, the endpoint does not provide evidence about the lotion groups’ efficacy, nor does it measure safety.

7. Results Posted in the Registry

• DFD01 Spray: 19.0% (33/174) versus 2.3% (2/87) on control; risk difference 16.7 percentage points (95% CI 10.0 to 23.3), risk ratio 8.25 (2.03–33.59); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The main posted outcome is binary: success means an IGA assessment of clear or almost clear at Day 15. For a binary outcome, the arm-level estimate is the proportion of participants with the event among the participants counted for that outcome. The registry record reports 33 successes among 174 participants for DFD01 Spray and 2 among 87 for Vehicle Spray, represented by percentages of 19.0% and 2.3%. This description concerns the observed endpoint counts; it does not imply that participants without a recorded success necessarily had a particular clinical status if missing-data handling is unknown.

What does the risk difference express?

The risk difference is the difference between the two success proportions on the probability scale. The unadjusted recalculation is 0.167, with a 95% confidence interval from 0.100 to 0.233. A confidence interval gives a range of values compatible with the data and the calculation method, under its assumptions. Its width reflects uncertainty in the estimated contrast. The interval does not mean that the true value has a specified probability of being inside this particular calculated interval.

The risk difference is an absolute contrast, unlike a ratio. It can be useful when the question concerns how far apart the observed proportions are on the original scale. The value is reported as calculated; no further conversion or derived percentage is needed to interpret its direction. The interval lies above zero, so the estimated contrast is positive throughout the stated interval.

Why report relative measures as well?

The risk ratio compares the event proportion in one group with the event proportion in the other. The recalculated risk ratio is 8.25, with a 95% confidence interval from 2.027 to 33.59. The odds ratio compares event odds instead and is 9.947, with a 95% confidence interval from 2.328 to 42.51. Ratios describe relative rather than absolute contrasts. They are not interchangeable with the risk difference, and the odds ratio is not the same quantity as the risk ratio.

The relative estimates have broad intervals. In general, relative measures can be imprecise when an outcome is uncommon or when one group has few events, because small changes in event counts can substantially affect a ratio. Here, the posted counts are 2 successes in the Vehicle Spray group and 33 in the DFD01 Spray group. The registry record does not give a separate precision calculation for the relative measures beyond their reported confidence intervals.

What does the p-value test?

The unadjusted recalculation gives p < 0.001. The registry record reports a Cochran-Mantel-Haenszel comparison with p < 0.001. A p-value describes how incompatible the observed data are with a specified null hypothesis, assuming the statistical model and test conditions are appropriate. It is not the probability that the null hypothesis is true, nor does it measure the probability that the result is due to chance in an everyday sense. It also does not communicate the size or precision of the contrast; those are better considered using the estimates and confidence intervals.

The sponsor’s reported method is Cochran-Mantel-Haenszel. This is a method for comparing groups while accounting for stratification when the relevant strata are defined. The registry record does not identify the strata or provide the method’s estimated effect and confidence interval. The unadjusted recalculation uses the posted summary counts and is not a substitute for details of the sponsor’s analysis. Since no discrepancy is flagged between the posted result and recalculation, the p-values are consistent at the reported threshold; the sponsor’s own analysis remains the primary reported analysis.

Why can over-dispersion matter?

In general, over-dispersion means that observed variation is greater than a model assumes. If a method assumes less variability than is actually present, standard errors can be too small and confidence intervals too narrow; tests may then appear more decisive than warranted. For a simple binary comparison, the event counts and chosen model determine the uncertainty calculation. The registry record does not report an over-dispersion assessment or a model that explicitly accounts for it, so no conclusion about over-dispersion in this trial can be made.

What analysis details remain unclear?

The record reports one primary outcome measure and one analysis. It does not give the full statistical analysis plan, the original analysis population definition, the randomization strata, adjustment variables, missing-data method, or whether any sensitivity analyses were conducted. The endpoint description says efficacy was only done for DFD01 Spray and Vehicle Spray; that statement establishes the scope of the posted efficacy comparison, but not whether the analysis was intention-to-treat, per-protocol, or another population definition. Those details are not reported in the registry record.

The primary endpoint is measured at Day 15, while the intervention descriptions specify treatment durations of 28 days for DFD01 Spray and Vehicle Spray. The record does not explain the rationale for the assessment timing or describe repeated outcome measurements. The available result should therefore be interpreted as the posted Day 15 binary comparison, rather than as a time course or a complete description of response over treatment.

10. Confidence Intervals and Precision

The arm-level estimates are 19.0% for DFD01 Spray and 2.3% for Vehicle Spray. Their 95% confidence intervals are 13.1% to 24.8% and 0.0% to 5.4%, respectively. These intervals communicate uncertainty in each group’s estimated success proportion. They do not establish that every value in the interval is equally plausible, and they do not account for design or analysis features that are not described in the registry record.

The unadjusted risk difference is 0.167, with a 95% confidence interval from 0.100 to 0.233. The interval excludes zero, indicating that values at or near no difference are not included within this calculated interval under its assumptions. The interval is more informative about the estimated contrast’s precision than the p-value alone, because it expresses a range on the risk-difference scale.

The relative estimates have wider ranges: the risk ratio is 8.25, with a 95% confidence interval from 2.027 to 33.59, and the odds ratio is 9.947, with a 95% confidence interval from 2.328 to 42.51. The small number of Vehicle Spray successes is important context for those estimates. Relative measures can become particularly unstable when one group has few observed events, and their intervals reflect substantial uncertainty about the magnitude of the relative contrast.

Confidence intervals describe sampling uncertainty under the method used; they do not cover every source of uncertainty. They cannot correct for missing data, measurement issues, selection effects, or unreported analysis choices. The registry record does not provide enough information to assess those issues in detail. The values should be read as estimates from the posted endpoint data, with the sponsor’s reported test and the unadjusted recalculation distinguished from one another.

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 based on the observed effect, not the trial’s original design calculation. The original sample-size justification and its assumptions are not reported in the registry record. The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers effects set at 100%, 75%, and 50% of the observed effect. The figures are participants per arm, not total events.

For planning at 100% of the observed effect, the illustration gives 53 participants per arm for 80% power and 70 participants per arm for 90% power. At 75% of the observed effect, the corresponding figures are 78 and 104 participants per arm. At 50% of the observed effect, they are 136 and 181 participants per arm. These are planning illustrations under the stated assumptions, not descriptions of the trial’s actual randomized allocation.

In general, power is the probability that a planned study will detect an effect of a specified size at the chosen significance level, if that effect is present and the planning assumptions hold. The 80% column means the illustrated design targets an 80% chance of detecting the chosen effect; the 90% column targets a 90% chance. The columns do not indicate the probability that the result is true or the probability that a treatment is beneficial. Smaller effects require more participants to detect with the same target power, which is why the entries increase as the assumed fraction of the observed effect decreases.

These figures are not observed power. They are prospective planning illustrations using an effect estimated from this trial’s posted data. The registry record does not report whether the trial’s actual design used the same 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 = 0.023; treatment proportion p₁ = 0.190; average p̄ = 0.106.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4359 = 0.8544.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4197 = 0.3532.
4. n = (0.8544 + 0.3532)² / (0.1667)² = 52.5, rounded up to 53 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 <- 0.0229885057471264                          # control proportion
p1 <- 0.189655172413793                          # 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(1947491)
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 = 53 (80% power), 70 (90% power)
 75% of observed effect: n per arm = 78 (80% power), 104 (90% power)
 50% of observed effect: n per arm = 136 (80% power), 181 (90% power)
power.prop.test: 52.5 
Simulated power at n = 53 per arm: 0.858 (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’s reported comparison uses the Cochran-Mantel-Haenszel method and gives p < 0.001 for the DFD01 Spray and Vehicle Spray groups. The unadjusted recalculation from the posted summary counts also gives p < 0.001. The reported analysis does not include an effect estimate or confidence interval in the registry record, so the recalculated risk difference, risk ratio, and odds ratio should be understood as separate unadjusted summaries rather than estimates from the sponsor’s method.

The recalculation gives a risk difference of 0.167, with a 95% confidence interval from 0.100 to 0.233. The relative measures are a risk ratio of 8.25, with a 95% confidence interval from 2.027 to 33.59, and an odds ratio of 9.947, with a 95% confidence interval from 2.328 to 42.51. These estimates use the posted group counts and do not reproduce any adjustment that may be part of the Cochran-Mantel-Haenszel analysis. The registry record does not identify any strata used by that method.

No discrepancy is flagged between the posted outcome and the recalculation. The sponsor’s own analysis is the reported inferential analysis; the recalculation helps express the observed contrast on familiar scales but cannot replace the sponsor’s method or recover unreported analysis details. The shared p-value threshold does not mean that the methods, estimands, or confidence intervals are identical.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome measure and one analysis, and it lists no posted secondary outcomes. This does not establish how many outcomes, time points, subgroups, or other analyses were considered in the full study. A multiplicity adjustment addresses the increased chance of false-positive findings when several hypotheses are tested. Whether an adjustment was planned or applied is not reported in the registry record.

The record gives a single primary endpoint at Day 15, but it does not provide the full statistical analysis plan or explain how the primary endpoint was selected. It also does not describe prespecified subgroup analyses, interim analyses, or any procedure for controlling the overall type I error rate across analyses. Those procedures are not reported in the registry record and should not be inferred from the single posted analysis.

Missing-data handling is also not described. The efficacy denominators are 174 for DFD01 Spray and 87 for Vehicle Spray, while the corresponding listed intervention counts for Comp01 Lotion and Vehicle Lotion are 0.0 for this endpoint. The record states that efficacy was only done for the spray groups. It does not say whether the efficacy denominators include all randomized participants in those groups, how missing Day 15 assessments were handled, or whether participants were excluded for other reasons. It is therefore not possible to determine from the registry record whether the result uses an intention-to-treat population, a per-protocol population, or another defined analysis population.

The record also does not report sensitivity analyses showing how alternative missing-data assumptions might affect the result. In general, missing outcomes can affect a binary success proportion if the likelihood of missingness is related to group assignment or outcome status. Without information about the number and reasons for missing assessments and the analysis method, the direction and size of any such effect cannot be assessed. This is a limitation of the available record, not evidence that missing data did or did not alter the estimate.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: diabetes mellitus (1.1%), convulsion (1.1%), alcohol withdrawal syndrome (1.1%), chronic obstructive pulmonary disease (1.1%), urinary tract infection (1.1%).

The safety record lists serious adverse events among participants at risk as 0 of 173 for DFD01 Spray, 1 of 87 for Vehicle Spray, 2 of 90 for Comp01 Lotion, and 0 of 43 for Vehicle Lotion. These are counts for the safety record and should be read separately from the Day 15 efficacy denominators. The serious-event counts do not by themselves identify the cause of an event or establish a difference between interventions.

The record lists other adverse events among 23 of 173 participants at risk with DFD01 Spray, 15 of 87 with Vehicle Spray, 19 of 90 with Comp01 Lotion, and 20 of 43 with Vehicle Lotion. These are distinct from the serious adverse event counts. The registry lists Diabetes Mellitus, Convulsion, Alcohol Withdrawal Syndrome, Chronic Obstructive Pulmonary Disease, Urinary Tract Infection, and Fall among the top serious event terms, each at 1.1%. The record does not identify the group assignment for those terms in the information.

Deaths are not reported in the registry record. The available counts do not provide event timing, severity details beyond the serious classification, causal attribution, or a comparative statistical analysis. They should therefore be treated as descriptive safety counts, not as proof of either safety or harm.

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

The posted efficacy data show a higher Day 15 IGA success proportion in the DFD01 Spray group than in the Vehicle Spray group: 19.0% versus 2.3%. The unadjusted risk difference is 0.167, and its 95% confidence interval is 0.100 to 0.233. The unadjusted p-value is <0.001, and the registry’s Cochran-Mantel-Haenszel analysis also reports p < 0.001. Together, these statistics describe a clear difference in the posted binary outcome under the analyses reported.

The estimates do not establish that the result applies to every participant or setting. They do not show how the outcome changes after Day 15, since no such result is posted as a secondary outcome. Nor do they provide efficacy evidence for Comp01 Lotion or Vehicle Lotion. The registry record explicitly limits the efficacy comparison to DFD01 Spray and Vehicle Spray. The record’s broader study objective also mentions safety comparison with Comp01 Lotion, but the posted primary efficacy result does not answer that safety question.

The result is specific to the definition of success: IGA clear or almost clear. It is not a measure of every aspect of psoriasis, an average change in disease severity, or a comprehensive account of participants’ experience. The registry record does not provide additional endpoint details, missing-data methods, or the complete analysis plan. The confidence intervals describe statistical precision under their calculation methods, but do not address all possible sources of bias or uncertainty.

The safety counts should be considered separately. They are descriptive event counts across four groups and do not establish causal attribution or a comparative safety conclusion. The registry record does not report deaths. Neither the efficacy statistics nor the safety counts, by themselves, support individual medical decisions. They describe the posted trial outcomes and their limits.

17. Why This Trial Matters Statistically

This trial is statistically notable because its registry record separates the stated study objectives from the posted primary efficacy result. Four interventions are listed, but the primary efficacy endpoint includes only DFD01 Spray and Vehicle Spray. The record expressly says efficacy was not done for Comp01 Lotion or its vehicle. Recognizing that distinction prevents the two-group efficacy result from being misrepresented as evidence comparing all four interventions.

The binary endpoint also illustrates why both absolute and relative measures can matter. The observed proportions are 19.0% and 2.3%; the unadjusted risk difference summarizes their separation on the probability scale, while the risk ratio and odds ratio describe relative contrasts. The relative estimates have broad confidence intervals, with only 2 successes in the Vehicle Spray group. This makes it important to consider uncertainty and event counts alongside a small p-value.

The registry reports a Cochran-Mantel-Haenszel test but does not identify its strata or provide an effect estimate from that method. The unadjusted recalculation offers additional descriptive estimates from the posted counts, while remaining distinct from the sponsor’s reported analysis. This is a useful example of why a reported test and a re-analysis should not be treated as interchangeable simply because they give the same p-value threshold.

Finally, the sample-size illustrations are based on the observed effect and explicit planning assumptions, rather than the trial’s original design rationale. That distinction matters: planning scenarios can help readers understand how required sample size changes with assumed effect size and target power, but they do not reveal the trial’s original power or design assumptions.

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 provides limited information about the trial’s statistical design and conduct. It does not report the original sample-size justification, the randomization ratio, the procedures used to generate or conceal allocation, or operational details of masking. The listed enrollment of 394 is not enough to reconstruct allocation or the analysis population. The record also does not describe eligibility criteria in detail or provide participant characteristics for the efficacy groups.

The primary efficacy result is limited to DFD01 Spray and Vehicle Spray. No efficacy result is posted for Comp01 Lotion or Vehicle Lotion, even though all four interventions appear in the trial record. The primary outcome is assessed at Day 15, and the record does not provide a fuller outcome trajectory or posted secondary outcomes. Conclusions about other interventions, times, or outcomes are therefore not supported by this endpoint.

Missing-data handling and the analysis population are not described. The registry does not explain whether the endpoint counts include every randomized participant in the spray groups, how unevaluable IGA assessments were treated, or whether sensitivity analyses were performed. The Cochran-Mantel-Haenszel method is named, but its strata and estimated effect are not reported. The complete statistical analysis plan, multiplicity procedures, subgroup methods, and interim analyses are also not reported in the registry record.

The safety information consists of posted counts and serious event terms. It does not give event narratives, timing, causal assessments, or comparative statistical tests. Deaths are not reported in the registry record. These omissions limit how fully the safety findings can be interpreted, and the descriptive counts should not be treated as a complete safety analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Comparison of DFD01 Spray Versus Comp01 Lotion, Vehicle Spray and Vehicle Lotion in Subjects With Moderate Psoriasis — NCT01947491.
• Registry record last updated 2024-03-07; status last verified 2024-03.
• Results first posted 2016-10-06.
• 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 record describes a completed, randomized, double-masked, parallel-group Phase 3 trial in psoriasis, with enrollment of 394. It lists DFD01 Spray, Vehicle Spray, Comp01 Lotion, and Vehicle Lotion. The primary endpoint is the percentage of participants with IGA success, defined as clear or almost clear, at Day 15.

Posted efficacy is limited to DFD01 Spray and Vehicle Spray. The success proportions are 19.0% and 2.3%; the unadjusted risk difference is 0.167, with a 95% confidence interval from 0.100 to 0.233. The sponsor’s Cochran-Mantel-Haenszel analysis reports p < 0.001, as does the unadjusted recalculation.

Safety counts are available for all four groups, but deaths are not reported in the registry record. Details of the original sample-size rationale, missing-data approach, analysis populations, and full statistical plan are also not reported in the registry record.