Dose Ranging Study To Assess Efficacy, Safety and Tolerability Of PF-06700841 Topical Cream In Psoriasis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dose Ranging Study To Assess Efficacy, Safety and Tolerability Of PF-06700841 Topical Cream In Psoriasis (NCT03850483), a randomized phase 2 study. The primary outcome is Change From Baseline in Psoriasis Area and Severity Index (PASI) Score at Week 12.

2. Clinical Question

The trial addresses a dose-ranging question, rather than a single comparison of one dose with a control. The primary endpoint is a continuous measure of psoriasis severity and extent; lower PASI scores represent less severe disease. The posted arm results describe average change, while the sponsor’s reported analyses compare least-squares means using ANCOVA. The registry record does not report the detailed dose-selection objective or the decision rule that would determine which dose, if any, merited further study.

3. Trial Design

This was a Phase 2b, randomized, double-blind, vehicle-controlled, parallel-group study of PF-06700841 topical cream in participants with mild to moderate chronic plaque psoriasis. The registry lists quadruple masking and a completed status. It reports enrollment of 344. The brief summary describes a planned enrollment of approximately 280 participants; these are distinct registry statements, and the record does not explain the difference between the planned and listed enrollment.

The study compared vehicle and active cream across once-daily and twice-daily schedules, with dose concentrations ranging from 0.1% to 3.0%. The listed study duration was approximately 22 weeks, including up to a 6 week screening period, a 12 week treatment period, and approximately 4 weeks of follow-up. The primary endpoint was change in PASI score at Week 12. Secondary outcomes included PGA response, PASI response and change measures at several visits, and PP-NRS scores.

The primary efficacy analysis set was not simply all randomized participants: it included randomized participants who received at least 1 dose and whose Week 12 visit was not missing due to the COVID-19 pandemic. The record does not report the detailed randomization procedure, allocation ratio, masking roles, or the sponsor’s original sample-size justification. The listed start date was 2019-04-08 and primary completion date was 2021-04-20. Those dates give study-record context but do not establish when individual participants were recruited or followed.

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.

Only the first 6 of 10 groups are shown.

Treatment for Stage 1

Reasons for not completing this period:

Follow-up for Stage 1

Reasons for not completing this period:

Treatment for Stage 2

Reasons for not completing this period:

Follow-up For Stage 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Efficacy analysis set (EAS) included all randomized participants who receive at least 1 dose of investigational product (PF-06700841 or placebo) and Week 12 visits were not missing due to COVID-19 pandemic.

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: Analysis population included participants who were randomly assigned to PF-06700841 and applied at least 1 dose of PF-06700841.

Only the first 6 of 10 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Psoriasis Area and Severity Index (PASI) Score at Week 12, measured over Baseline, Week 12.

The primary endpoint was change from baseline in the Psoriasis Area and Severity Index score at Week 12. PASI combines assessments of disease severity and affected body surface area across the head, arms, trunk, and legs. Within each region, the assessment considers erythema, induration, and scaling. The registry describes PASI as a scale from 0 to 72, with higher scores representing greater severity.

Change from baseline expresses how the score shifted during the study rather than the score at a single visit. A negative change indicates that the Week 12 score was lower than baseline; in the endpoint’s direction, a larger reduction corresponds to a greater decrease in measured severity. The endpoint is continuous, so the posted arm values are least-squares means and their dispersion is reported as standard errors.

PASI is used in this trial because it combines severity and extent into one outcome, allowing the study to compare average changes across dose and schedule groups. It does not describe every aspect of psoriasis or how participants felt, and it should not be read as an individual-level outcome. The registry does not report a threshold for a clinically important difference on this endpoint, so the clinical importance of a particular numerical contrast is not established by the endpoint description alone.

7. Results Posted in the Registry

• PF-06700841 0.1% QD: mean -2.20 versus -1.60 on control; difference -0.60 (95% CI -1.88 to 0.68), standardized effect d = -0.22; z-test p = 0.356.
• PF-06700841 0.3% QD: mean -1.40 versus -1.60 on control; difference 0.20 (95% CI -1.08 to 1.48), standardized effect d = 0.07; z-test p = 0.759.
• PF-06700841 1.0% QD: mean -2.20 versus -1.60 on control; difference -0.60 (95% CI -1.88 to 0.68), standardized effect d = -0.22; z-test p = 0.356.
• PF-06700841 3.0% QD: mean -2.40 versus -1.60 on control; difference -0.80 (95% CI -2.06 to 0.46), standardized effect d = -0.29; z-test p = 0.214.

8. Secondary Efficacy Endpoints

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

Percentage of Participants With Physician Global Assessment (PGA) Score Clear (0) or Almost Clear (1) and Greater Than or Equal to (>=) 2 Points Improvement From Baseline at Week 12

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • PF-06700841 0.1% QD: 10.3% (3/29) versus 6.9% (2/29) on control; risk difference 3.4 percentage points (95% CI -11.0 to 17.9), risk ratio 1.50 (0.27–8.32); unadjusted two-proportion z-test p = 0.640.
  • PF-06700841 0.3% QD: 15.4% (4/26) versus 6.9% (2/29) on control; risk difference 8.5 percentage points (95% CI -8.2 to 25.1), risk ratio 2.23 (0.44–11.19); unadjusted two-proportion z-test p = 0.313.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PF-06700841 0.1% QD and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PF-06700841 0.3% QD and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the assessment beyond average PASI change. They include PGA response, PASI response thresholds, PASI change and percent change at multiple visits, and PP-NRS scores. The registry lists 21 posted secondary outcomes. Taken together, these measures cover categorical improvement, continuous disease-severity change, persistence of change over follow-up visits, and itch-related scores.

The posted PGA results and their sponsor-reported comparisons do not resolve the uncertainty in the primary endpoint. In the two sponsor-reported PGA comparisons, the 90% confidence intervals for the risk difference include 0. The broader secondary outcome set may help describe patterns across measures and visits, but the record does not support treating those outcomes as independent confirmations of the primary analysis.

Many outcomes, doses, schedules, and time points create multiple opportunities for apparently notable results. Unless a prespecified multiplicity procedure controls the overall chance of false-positive findings, unadjusted secondary p-values should carry less weight than results from a prespecified primary comparison. The registry record does not report a multiplicity adjustment plan or a hierarchy for interpreting secondary endpoints. It is therefore more appropriate to view the secondary results as supportive and exploratory rather than as a basis for overriding the primary ANCOVA results.

The secondary analyses also have their own denominators and uncertainty, and those may differ across outcomes. The registry record does not give a complete account of outcome-specific missingness or analysis populations for every secondary measure. Patterns across secondary endpoints can provide context, but they do not establish a coherent treatment effect simply because several measures were recorded. The relevant interpretation remains one of estimates, precision, and the analysis methods reported for each outcome.

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

• Percentage of Participants With Physician Global Assessment (PGA) Score Clear (0) or Almost Clear (1) and Greater Than or Equal to (>=) 2 Points Improvement From Baseline at Week 12
• Percentage of Participants With 75% Reduction From Baseline in PASI at Week 1, 2, 4, 6, 8, 10, 12, 14, and 16
• Change From Baseline in PASI Scores at Week 1, 2, 4, 6, 8, 10 and 12
• Change From Baseline in PASI Scores at Week 14 and 16
• Percent Change From Baseline in PASI Scores at Week 1, 2, 4, 6, 8, 10 and 12
• Percent Change From Baseline in PASI Scores at Week 14 and 16
• Absolute Peak-Pruritus Numerical Rating Scale (PP-NRS) Score at Baseline, Week 1, 2, 4, 6, 8, 10 and 12
• Absolute PP-NRS Score at Week 14 and 16

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant’s PASI score can take a range of values, and the analysis summarizes the amount of change. The registry reports least-squares means for the arms, with standard errors as the dispersion measure. A least-squares mean is an adjusted mean from a statistical model; it is not necessarily the same quantity as a simple arithmetic average. The registry record does not provide the full ANCOVA model specification, including the covariates used or the details of its assumptions.

What does an arm mean describe?

An arm’s Week 12 change summarizes the average change for the participants included in that arm’s analysis. For example, the vehicle once-daily arm has a posted mean change of -1.6, while PF-06700841 1.0% BID has a posted mean change of -3.0. These means describe within-arm change. Comparing them informally is not a substitute for the sponsor’s modeled between-group analysis, particularly when the analysis uses least-squares means and adjusts for model terms.

What does a mean difference describe?

A between-group mean difference expresses the estimated contrast between an active-treatment group and its vehicle comparator. In this endpoint, a negative difference means the estimated change is more negative in the PF-06700841 group than in the corresponding vehicle group. The sponsor reports these contrasts as LS mean differences from ANCOVA. The registry lists 90% confidence intervals and p-values for those reported comparisons. A confidence interval conveys a range of values compatible with the data and the analysis assumptions; it does not guarantee that the true effect lies inside that interval.

Why distinguish the sponsor analysis from a recalculation?

The recalculated comparisons are simple, unadjusted calculations based on posted arm summary statistics. They use the means and standard errors rather than reproducing the sponsor’s ANCOVA model. The standard deviations used in those calculations are approximate, as indicated by the recalculation description. Such calculations can be useful for orientation, but they do not recover an adjusted model when the full participant-level data and model specification are unavailable. Since the recalculated results conflict with the sponsor’s reported results, the sponsor’s own analysis takes precedence.

The difference between analyses can arise because they answer closely related but not identical statistical questions. An unadjusted contrast of posted summaries does not account for covariates that may have entered the sponsor’s ANCOVA. It may also use approximations to variability rather than the model-based covariance structure. The registry record does not give enough model detail to attribute the discrepancy to a particular feature. It is therefore more accurate to report both analyses with their status made clear than to treat the recalculation as a correction.

Why is over-dispersion relevant in general?

In general, over-dispersion means that observed variability is greater than a model’s assumed variability. When a model underestimates variability, standard errors can be too small and intervals too narrow. The primary endpoint is continuous, and its posted dispersion is a standard error; the registry record does not identify an over-dispersion adjustment for the primary analysis. Over-dispersion is not a finding established by these results. It is a general consideration when assessing whether a statistical model adequately represents outcome variability.

What do the binary secondary outcomes represent?

Some secondary outcomes are proportions, such as the percentage reaching a PGA category and improvement threshold at Week 12. A risk difference compares the proportions directly, in percentage-point terms when expressed as percentages. The registry’s sponsor-reported binary comparisons use the Chan and Zhang method and report 90% confidence intervals. The recalculated risk differences use the posted counts and group sizes and are unadjusted. With relatively few observed responses in the listed comparisons, the intervals are wide; an imprecise estimate should not be read as evidence that the groups are identical.

Finally, the record lists many outcome measures and analyses. Statistical significance from an individual comparison does not account automatically for the number of comparisons examined. Without a reported multiplicity plan, the interpretation of isolated nominal p-values is limited. The record also does not report the complete statistical analysis plan, interim analyses, or a detailed missing-data method, so those features cannot be inferred from the results.

11. Confidence Intervals and Precision

Confidence intervals describe the uncertainty around an estimated contrast under the specified analysis. Narrower intervals indicate greater statistical precision, while wider intervals permit a broader range of possible effects. The sponsor reports 90% confidence intervals for the primary ANCOVA comparisons. All of those intervals include 0, so the reported estimates are compatible with no between-group difference as well as with effects in either direction.

The reported intervals are not especially tight relative to the estimates. For example, the sponsor’s comparison of PF-06700841 1.0% BID with pooled vehicle BID is -0.8, with a 90% confidence interval from -1.88 to 0.29. The interval crosses 0 and includes both a more negative estimated change in the active group and a less negative change. The other reported primary intervals also cross 0. This is uncertainty about the size and direction of the contrast, not proof of no effect.

The recalculated intervals differ because they are simple unadjusted estimates from posted summary statistics rather than the sponsor’s ANCOVA. The PF-06700841 1.0% BID recalculated interval is -2.746 to -0.054, while the sponsor-reported 90% interval for that comparison is -1.88 to 0.29. The discrepancy makes it especially important not to select whichever interval appears more decisive. The sponsor’s own analysis takes precedence.

For the PGA responder outcome, the sponsor-reported 90% intervals for the two comparisons extend from negative to positive risk differences. The posted responder proportions also have uncertainty intervals. These ranges reflect limited precision in the observed response estimates. The registry record does not report a prespecified clinically meaningful difference for either outcome, so the statistical intervals alone do not identify a threshold for practical importance.

12. Planning a Similar Trial: Sample Size

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

The sample-size display is a planning illustration based on the observed effect, not the trial’s original design calculation. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. For these continuous and binary examples, the entries are participants per arm; the note that time-to-event displays would give total events does not apply to these outcomes.

The 80% power column gives the planning number of participants per arm for a design with an 80% chance of detecting the assumed effect at the stated significance level, if the assumptions hold and the effect is real. The 90% power column gives the corresponding planning number for a 90% chance. These are design targets, not probabilities that the observed trial result is true. Smaller effects require more participants to distinguish them from random variation, so the planning entries rise when the assumed effect is reduced from 100% to 75% or 50% of the observed effect.

The displayed figures are not observed power. Observed power is not a useful substitute for interpreting the estimate and its confidence interval after a study has been completed; the planning figures instead illustrate how sample-size requirements depend on the effect size assumed for a future design. They should not be treated as the number actually needed for a confirmatory trial without considering the intended analysis, multiplicity, population, missing data, and a clinically meaningful target effect. The registry record does not report the assumptions behind the trial’s own original design or sample-size justification.

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 = -0.600; pooled standard deviation σ = 2.779.
2. n = 2 × (1.96 + 0.842)² × 2.779² / -0.600² = 336.8, rounded up to 337 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 <- -0.6                      # observed difference in means
sigma <- 2.77936865867863                     # 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(3850483)
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 = 337 (80% power), 451 (90% power)
 75% of observed effect: n per arm = 599 (80% power), 802 (90% power)
 50% of observed effect: n per arm = 1,348 (80% power), 1,804 (90% power)
power.t.test: 337.8 
Simulated power at n = 337 per arm: 0.802 (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. Analyses Reported by the Sponsor

The sponsor’s primary comparisons are ANCOVA estimates of LS mean difference, with 90% confidence intervals and p-values. These should guide interpretation of the trial’s reported primary analysis. The recalculated contrasts are unadjusted re-estimates from the posted arm means and standard errors; they do not reproduce the ANCOVA model.

The difference is material for PF-06700841 1.0% BID versus pooled vehicle BID: the recalculation gives a mean difference of -1.4, interval -2.746 to -0.054, and p = 0.042, whereas the sponsor reports an LS mean difference of -0.8, 90% confidence interval -1.88 to 0.29, and p = 0.113. The sponsor’s interval includes 0; the recalculated interval does not. This is why the recalculated result should not be presented as the study’s own finding.

Other comparisons also show numerical differences in estimates, intervals, or p-values. The registry record does not provide enough information to explain the discrepancy, including the full ANCOVA specification. The sponsor’s own analysis takes precedence, and the unadjusted recalculations are best regarded as a transparent sensitivity to how posted summaries might be compared, not a replacement for the reported analysis.

15. Multiplicity, Missing Data and Analysis Populations

The study compares several PF-06700841 doses and schedules with vehicle, and the registry lists a broad set of secondary outcomes and analyses. Each additional comparison creates another opportunity for a nominally small p-value to occur by chance. A multiplicity procedure can control the overall false-positive risk across a family of comparisons, but no such procedure is described in the registry record. The record also does not report whether the primary comparisons were organized into a prespecified testing hierarchy. Without that information, isolated p-values, especially among secondary outcomes, should be interpreted cautiously.

The primary analysis population is defined as the efficacy analysis set: randomized participants who received at least 1 dose and whose Week 12 visits were not missing due to the COVID-19 pandemic. This definition identifies who was included but does not fully explain how missing outcome data were handled. The registry record does not report imputation methods, sensitivity analyses for missing outcomes, or the number excluded specifically because a Week 12 visit was missing due to the pandemic. Those details matter because the analyzed population may differ from all randomized participants.

The record also does not report a detailed statistical analysis plan, the original sample-size justification, interim analyses, or all model specifications. It is therefore not possible to establish from the posted registry information whether every analysis was prespecified or how alternative analytic choices would affect the estimates. These are limitations in what can be concluded from the record, not evidence that any particular method was or was not used.

Finally, participant counts vary between endpoint summaries and safety groups, and the registry does not explain every difference in denominators. The appropriate denominator is the one attached to the specific outcome and analysis, rather than an assumed common population across the entire study.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: thrombophlebitis septic (2.8%), urinary tract infection (2.8%), aspiration bursa (2.8%), lethargy (2.8%), depression (2.8%).

The safety summary reports serious adverse events, other adverse events, and deaths by group. The serious-event counts range from 0 to 2 across the listed groups; the record reports one death in the pooled vehicle BID group and none in the other listed groups. These are counts as reported, not rates calculated for comparison. The group at-risk counts differ, so the counts should be read with their listed denominators and not compared as if each group had the same size.

The registry lists six top serious-event terms, each at 2.8%: thrombophlebitis septic, urinary tract infection, aspiration bursa, lethargy, depression, and pulmonary embolism. The posted summary does not assign those terms to specific treatment groups in the information available for this description. It also does not establish that an event was caused by study treatment. These figures describe reported events in the registry record; they do not by themselves estimate comparative safety or provide a complete account of event timing, severity, or relatedness.

Safety counts should be considered alongside the duration and population studied. The registry record does not report enough detail to draw causal conclusions about treatment and adverse events.

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

The results describe a randomized, vehicle-controlled dose-ranging study and show the posted average PASI change through Week 12 for each group. Each group had a negative mean change, while the sponsor-reported between-group estimates were imprecise: all listed primary 90% confidence intervals include 0. The observed differences therefore do not establish a precise separation between PF-06700841 and vehicle for the reported primary comparisons.

That interpretation is not the same as saying that the treatments are equivalent or that no difference exists. Intervals that include 0 leave room for effects in either direction, and the study’s estimates have uncertainty. Nor does a numerical trend across a few dose groups establish a dose-response relationship. The registry results do not show a consistent pattern in which estimated change improves steadily with higher concentration or more frequent application.

The recalculated analysis of PF-06700841 1.0% BID differs from the sponsor’s ANCOVA result. Because of this discrepancy, the sponsor’s reported analysis takes precedence; the recalculation should not be used to claim a definitive positive finding. The record does not describe the full model needed to reconcile the two analyses.

The findings also do not establish whether the magnitude of any difference would be clinically meaningful. The registry record does not specify a minimal clinically important PASI difference. Secondary outcomes add context, but their multiplicity and missing-data details are not reported sufficiently to treat nominal results as independent confirmation. Safety counts are descriptive and cannot establish that events were caused by treatment.

In short, the registry record supports a description of the observed arm changes and reported comparisons, with substantial uncertainty around between-group differences. It does not establish treatment benefit, equivalence, a definitive dose choice, or a causal safety conclusion.

18. Why This Trial Matters Statistically

This trial is statistically useful as an example of why a dose-ranging design should be interpreted through estimates and uncertainty rather than arm means alone. Negative within-arm changes occurred in the vehicle groups as well as in the active-treatment groups. A change from baseline in an active arm therefore does not isolate the effect of treatment; the between-group contrast is the relevant estimate for that question.

The record also illustrates the distinction between a sponsor’s model-based analysis and an unadjusted recalculation from summary statistics. The recalculated PF-06700841 1.0% BID comparison appears more decisive than the sponsor’s ANCOVA comparison, but it does not reproduce the sponsor model. When analyses disagree, the reported trial analysis should not be displaced by a simpler calculation that may use different assumptions.

The number of dose, schedule, and outcome comparisons makes multiplicity an important interpretive issue. A nominally notable result is less persuasive when the analysis plan does not indicate how multiple testing was handled. At the same time, the posted estimates and intervals remain informative: they show the range of effects compatible with each analysis and indicate where the data are imprecise.

Finally, the record’s population definition and outcome-specific denominators matter. Readers should distinguish the efficacy analysis set from all randomized participants and avoid assuming that every endpoint includes the same participants. These statistical distinctions are relevant to interpreting this particular trial without overclaiming what the registry data establish.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record has important limits for interpreting the results. The full ANCOVA specification is not reported, so the covariates, model assumptions, and other details underlying the sponsor’s primary comparisons cannot be evaluated from the record alone. The discrepancy between sponsor-reported and recalculated comparisons remains unexplained; the sponsor’s analysis takes precedence, but the available information does not identify the source of the difference.

The original sample-size justification and statistical analysis plan are not reported. The planning illustrations based on observed effects do not establish the study’s original power or design assumptions. The record does not report a multiplicity adjustment for the many dose, schedule, outcome, and visit comparisons, limiting the weight that should be given to isolated nominal p-values.

The efficacy analysis set excludes randomized participants who did not receive at least 1 dose and those whose Week 12 visits were missing due to the COVID-19 pandemic. The number of participants excluded for each reason, the handling of other missing values, and sensitivity analyses are not reported in the information available. As a result, the implications of missing data for the estimates cannot be assessed fully.

The registry’s planned enrollment was approximately 280 while its listed enrollment was 344; the record does not explain this difference. It also does not provide an endpoint-specific explanation for all variations in group denominators. Finally, the endpoint description gives no threshold for clinically meaningful PASI change. Statistical differences therefore cannot be translated directly into clinical importance from the record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Dose Ranging Study To Assess Efficacy, Safety and Tolerability Of PF-06700841 Topical Cream In Psoriasis — NCT03850483.
• Registry record last updated 2022-06-29; status last verified 2022-06.
• Results first posted 2022-06-29.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT03850483 is a completed Phase 2b randomized, double-blind, vehicle-controlled, parallel-group dose-ranging study of topical PF-06700841 in mild to moderate chronic plaque psoriasis. Listed enrollment was 344, and the primary endpoint was change from baseline in PASI score at Week 12.

All groups had negative mean PASI changes. The sponsor-reported ANCOVA comparisons had 90% confidence intervals that included 0. A simple unadjusted recalculation differs from the sponsor analysis for at least one comparison; the sponsor’s own analysis takes precedence. The registry lists multiple secondary outcomes and descriptive safety counts, but does not report a multiplicity plan or the full statistical analysis plan.