A Study to Evaluate Long-Term Maintenance Treatment With Once Daily Crisaborole Ointment 2% in Pediatric and Adult Participants With Mild-to-Moderate Atopic Dermatitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate Long-Term Maintenance Treatment With Once Daily Crisaborole Ointment 2% in Pediatric and Adult Participants With Mild-to-Moderate Atopic Dermatitis (NCT04040192), a randomized phase 3 study. The primary outcome is Duration of Flare-Free Maintenance Until Onset of First-Flare During the Double Blind (DB) Period.

2. Clinical Question

This is a maintenance question in a responder population, not a comparison of starting crisaborole with starting vehicle in all people with atopic dermatitis. The result therefore speaks to the randomized maintenance phase among participants who had already responded to twice-daily crisaborole. It does not directly describe people who did not respond during that earlier treatment period, or the effect of beginning treatment without that preceding response-based selection.

The registry record identifies the condition as atopic dermatitis and describes the trial as a phase 3 randomized study with quadruple masking. The primary endpoint was time-to-event: the event was the first flare, and participants without an observed flare before the relevant censoring point contributed time until their last ISGA assessment. The clinical question is consequently about the timing of a first flare, rather than simply the proportion of participants who experienced any flare or the total number of flares.

3. Trial Design

The registry describes a phase 3, randomized, double-blind, vehicle-controlled study of once-daily crisaborole ointment, 2%, for maintenance treatment and flare reduction. The planned treatment period was up to 52 weeks. The study was conducted in pediatric and adult participants aged 3 months and older with mild-to-moderate atopic dermatitis who responded to twice-daily crisaborole treatment.

The randomized maintenance arms were vehicle once daily and crisaborole, 2%, once daily. The primary outcome record reports 129 participants in the vehicle arm and 125 in the crisaborole arm for the endpoint analysis. These are endpoint-analysis group counts; the registry enrollment figure of 620 describes the overall study enrollment and should not be interpreted as the number in either maintenance arm.

The primary endpoint was analyzed in the Eval-DB population. The record defines that population as randomized participants who had met the ISGA response criterion and EASI50 criterion at randomization. The ISGA criterion was clear or almost clear, with at least a 2-grade improvement from run-in baseline. This restriction means the maintenance comparison concerns responders meeting the stated criteria, rather than everyone enrolled in the study.

The registry reports the study as completed. Its recorded start date is 2019-09-12, and its primary completion date is 2022-01-19. The record lists Pfizer as sponsor. The specific randomization sequence, allocation-concealment procedures, and operational details of masking are not reported in the registry record. Nor is a fuller description of the earlier twice-daily treatment period reported in the primary endpoint record.

The control was vehicle ointment, which allows the randomized comparison to address maintenance assignment within the study design. The record does not report enough detail to determine how the planning enrollment related to the size of the responder population ultimately randomized to maintenance, or how the planned enrollment was justified.

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: A total of 620 participants signed the informed consent form and were enrolled in the study. 78 participants were screen failures who did not meet eligibility criteria. 542 participants were not screen failures, of which only 497 were assigned to study treatment.

Open Label Run-in Period (up to 8 Weeks)

Reasons for not completing this period:

Double Blind Period (up to 52 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Evaluable-DB (Eval-DB) population included all randomized participants with success in ISGA (i.e., achieving a score of clear \[0\] or almost clear \[1\] with a \>=2 grade improvement from the run-in baseline) and Eczema Area Severity Index score (EASI50) criteria as responders at randomization and received at least 1 dose of study intervention in the DB period.

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: Evaluable OL population comprised of all participants who received at least 1 dose of study intervention in the OL period.

6. Primary Endpoint

The registry lists the primary outcome as Duration of Flare-Free Maintenance Until Onset of First-Flare During the Double Blind (DB) Period, measured over From randomization to first flare or last ISGA assessment (up to 52 weeks).

The primary endpoint was the duration of flare-free maintenance until the first flare during the double-blind period. It was measured in days from randomization to the first flare, or to the last ISGA assessment when a participant had not experienced a first flare before an intercurrent event or the end of the study. The registry states that deaths, dropouts, loss to follow-up, and study end could lead to right censoring before a first flare.

This endpoint is useful for a maintenance question because it incorporates both whether a flare occurs and when it occurs. A simple count of participants with a flare would not distinguish an early event from one occurring much later. Time-to-event analysis retains information about the timing of the event and can also account for participants whose event time is not observed through the end of follow-up.

The endpoint was estimated using the Kaplan-Meier method. The reported arm summaries are medians with 95% confidence intervals. The median is the estimated time by which half of the analyzed population has experienced the event, subject to the time-to-event estimation and censoring procedures. It is not an average duration, and it does not imply that every participant had an event at or near the median.

The record defines the endpoint timeframe as from randomization to first flare or last ISGA assessment, up to 52 weeks. It also describes the flare-free duration as time to the last ISGA assessment when an intercurrent event occurred before the first flare. How other types of missing assessments were handled is not reported in the registry record.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

What does a time-to-event endpoint contribute?

In general, time-to-event methods use information about both the occurrence and timing of an event. Participants who have the event contribute an observed event time. Participants who leave follow-up or reach the end of observation without an event contribute information up to the point at which they were last known to be observed. This latter situation is called censoring; it is not the same as observing that no event will ever occur.

For this study, the event was a first flare. The registry says that a participant’s time was right censored if an intercurrent event, such as death, dropout, loss to follow-up, or end of study, occurred before the first flare. If a flare occurred first, the time from randomization to that flare was not censored. The record describes the endpoint time as ending at the first flare or last ISGA assessment, with follow-up up to 52 weeks. The handling of missing data beyond these stated censoring rules is not reported in the registry record.

How does Kaplan-Meier estimation work?

In general, the Kaplan-Meier method estimates the probability of remaining event-free over time while retaining censored participants’ observed follow-up up to their censoring time. It does not treat a censored participant as if the event occurred at the censoring time. The method relies on assumptions about censoring, including that censoring does not systematically carry unaccounted information about the future event process. The registry identifies Kaplan-Meier estimation but does not report diagnostic checks or sensitivity analyses for that assumption.

A median time-to-event estimate is the time at which the estimated event-free curve reaches the halfway point. It is a summary of the estimated distribution, not a mean and not a guarantee about an individual participant’s time to flare. The 95% confidence interval expresses uncertainty about the estimated median. It does not mean that 95% of participant times fall inside the interval.

What does the log-rank test compare?

In general, the log-rank test compares event-time experience between groups over the observed follow-up. It considers when events occur and how many participants remain at risk at those times, and it accommodates right-censored observations under its assumptions. A p-value from this test measures how incompatible the observed comparison is with the null hypothesis of no difference in event-time distributions, under the test model. It is not an effect-size estimate and does not indicate the probability that one treatment is better than another.

The registry reports a log-rank method and p-value for the primary endpoint, but no hazard ratio or confidence interval for a relative effect. A hazard ratio would summarize a relative event rate under a proportional-hazards interpretation; it is not interchangeable with a ratio of medians. Because the registry does not report that estimate for the primary comparison, it should not be inferred from the medians or the p-value.

How should the secondary continuous-outcome recalculations be read?

The recalculated mean differences use the posted arm-level summary statistics. They are unadjusted recalculations and need not match an analysis that adjusts for covariates or uses a different model. For number of flare-free days, the recalculated difference is 34.59 days, with a 95% confidence interval from 1.117 to 68.06 and an unadjusted p-value of 0.043. The registry separately reports an ANCOVA least-squares mean difference of 34.59 days, with a 95% confidence interval from 2.53 to 66.64 and p = 0.035. The registry’s analysis is the sponsor’s own reported analysis and takes precedence over the recalculation for describing the trial’s result.

For duration of flare period, the recalculated mean difference is 1.1 days, with a 95% confidence interval from -8.578 to 10.78 and an unadjusted p-value of 0.824. No sponsor-reported analysis is listed for that comparison. In general, a confidence interval that includes zero is compatible with no mean difference as well as with differences in either direction under the analysis assumptions. It does not prove that the groups are identical.

Why can over-dispersion matter?

In general, over-dispersion occurs when outcome variability is greater than a statistical model assumes. If a model underestimates variability, its standard errors can be too small and its confidence intervals too narrow, which can make evidence appear more precise than it is. Count outcomes such as numbers of flares can be especially sensitive to differences between the observed variation and a model’s assumed variation. The registry record does not report enough detail about a count-outcome model or its dispersion assumptions to assess this issue for the listed flare-count outcome.

What are the sample-size illustrations?

In general, sample-size planning asks how many participants might be needed to detect a chosen effect under stated assumptions. The posted planning illustrations use the observed effect or a stated fraction of it, a two-sided significance level of 0.05, equal allocation, and a normal approximation. They are planning illustrations, not the trial’s design justification and not observed power. The registry does not report the protocol’s sample-size justification or enough information to treat these illustrations as the original planning assumptions.

The registry notes that time-to-event planning displays use total event counts, while other displays use participants per arm. Such calculations depend on assumptions about the effect to detect and the analysis framework. They cannot establish how likely the completed trial was to produce a statistically significant result after the fact, and they do not replace the observed estimates, confidence intervals, or sponsor-reported analysis.

10. Analyses Reported by the Sponsor

For the primary time-to-first-flare outcome, the registry reports arm-specific Kaplan-Meier medians and a log-rank p-value. It does not report a hazard ratio or a confidence interval for a relative effect. There is therefore no primary sponsor estimate in the record to compare with a recalculated hazard ratio, and no such estimate should be derived from the arm medians.

For number of flare-free days, the registry reports an ANCOVA least-squares mean difference of 34.59 days, with a 95% confidence interval from 2.53 to 66.64 and p = 0.035. The unadjusted recalculation from the posted summary statistics gives the same stated difference, 34.59 days, but a 95% confidence interval from 1.117 to 68.06 and an unadjusted p-value of 0.043. This difference in interval and p-value is consistent with the distinction between an adjusted ANCOVA analysis and a simple unadjusted recalculation. The record does not provide enough detail to reproduce the sponsor model independently.

No sponsor-reported analysis is listed for duration of flare period. Its recalculated estimate is therefore only an unadjusted analysis of posted summary statistics, not a replacement for a sponsor analysis. Where a sponsor analysis is reported, that analysis takes precedence for describing the trial’s reported result. The registry does not report whether secondary-outcome multiplicity was addressed.

11. Multiplicity, Missing Data and Analysis Populations

The primary outcome is a time-to-first-flare measure, and the registry reports a log-rank comparison. The record does not report a detailed statistical analysis plan describing the full testing hierarchy, whether the primary test was the sole confirmatory hypothesis, or how secondary outcomes were to be interpreted if the primary comparison was not significant. A prespecified hierarchy can help control the chance of false-positive claims when many outcomes are tested; whether such a strategy was used is not reported in the registry record.

The record lists 100 secondary outcomes and reports multiple analyses. It does not report whether p-values for secondary outcomes were adjusted for multiplicity, whether selected outcomes were protected by a testing sequence, or whether the displayed secondary results are exploratory. Consequently, nominal secondary p-values should not be read as if each came from a single isolated test. The primary endpoint and secondary outcomes also measure different features of the disease course, so the number of outcomes is not the only consideration in interpreting their consistency.

For the primary endpoint, the record specifies that time was right censored when an intercurrent event occurred before a first flare, including death, dropout, loss to follow-up, or end of study. It also describes duration as ending at the last ISGA assessment if censoring occurred before the first flare. The record does not report the number of censored observations, reasons by arm, a detailed missing-data strategy for other missing assessments, or sensitivity analyses under alternative assumptions about missingness or censoring. Those omissions limit assessment of how strongly the primary estimate depends on the censoring process.

The Eval-DB population was restricted to randomized participants who met the stated ISGA and EASI50 response criteria at randomization. The registry does not report additional details about handling protocol deviations, missing eligibility measures, or analysis-population exclusions. It also does not report whether the primary result was checked in another population or under other analytic assumptions. These details matter because the reported population defines the scope of the result and because missing outcomes can affect time-to-event estimates if censoring is informative.

12. 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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: maternal exposure during pregnancy (1.5%), pneumonia (1.3%), foreign body ingestion (1.1%), cardiac failure congestive (0.7%), cardiomyopathy (0.7%).

The registry’s safety record includes serious adverse event counts for several study groups, including open-label twice-daily crisaborole, double-blind vehicle, double-blind once-daily crisaborole, and flare-related groups. In the open-label crisaborole 2% BID group, 3 serious adverse events were reported among 497 at risk; in the double-blind vehicle group, 3 were reported among 135 at risk; and in the double-blind crisaborole 2% QD group, 2 were reported among 135 at risk. The double-blind flare groups each report 1 serious adverse event, among 89 at risk for vehicle and 78 at risk for crisaborole 2% QD.

These are group-level counts from the registry record. They should not be interpreted as a randomized comparison across all listed groups: the open-label group and the double-blind maintenance groups reflect different study periods, and the flare groups are separately identified. The registry does not provide a statistical comparison or confidence intervals for these serious adverse event counts.

The record lists zero deaths in each of the reported groups. It also lists several serious adverse event terms with percentages, including maternal exposure during pregnancy at 1.5% and pneumonia at 1.3%. These event-term percentages should be read as the registry reports them; the record does not provide enough information to infer a causal relationship to treatment or to compare risks across groups. Adverse event counts are descriptive and do not by themselves establish whether a treatment caused an event.

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

The primary result describes estimated time to a first flare among participants who responded to twice-daily crisaborole and met the stated response criteria at randomization. In that selected maintenance population, the registry reports different Kaplan-Meier median estimates for once-daily crisaborole and vehicle, together with a log-rank p-value. This is evidence about the randomized maintenance comparison in the analyzed population, not a universal estimate for all people with atopic dermatitis.

The result does not show that every participant assigned to crisaborole remained flare-free for the arm median, nor that every participant assigned to vehicle experienced a flare at its median. Medians summarize estimated group distributions. Censoring means some participants’ first flare times were not observed before their follow-up ended, and the interpretation depends on the time-to-event assumptions and analysis choices described in the record.

The finding also does not answer whether crisaborole would have the same effect as an initial treatment, whether it benefits people who did not respond to twice-daily treatment, or how outcomes would compare in populations outside the stated eligibility and response criteria. The trial’s randomized phase tested once-daily maintenance against vehicle after the preceding response-based treatment stage.

A p-value does not measure the clinical importance of an effect, the probability that a result is true, or the likelihood that an individual will experience a particular outcome. The median estimates, confidence intervals, and comparison test address different aspects of the result: estimated timing, uncertainty around each median, and evidence of a difference in event-time distributions. The registry does not report a hazard ratio for the primary comparison, so a relative event-rate interpretation is not available from the posted primary results.

Finally, the result does not settle questions about longer-term outcomes beyond the study’s follow-up, uncommon adverse effects, or the overall balance of benefits and harms. The safety counts are descriptive and the registry does not report inferential comparisons for those counts. The appropriate statistical conclusion is limited to the outcomes, study population, treatment assignments, and follow-up recorded in the trial.

14. Why This Trial Matters Statistically

This trial is statistically informative because its primary outcome matches a maintenance question: not simply whether a first flare occurred, but how long participants remained without one. Time-to-event analysis can preserve timing information and account for participants whose observed follow-up ends before an event. The registry also makes the censoring definition explicit enough to identify key assumptions that readers should consider.

The responder-based design defines a focused population. It examines maintenance among participants who had responded to the preceding twice-daily treatment and met the response criteria at randomization. That design can be useful for evaluating a continuation strategy in responders, but it narrows the population to which the randomized comparison directly applies. The distinction between the overall enrollment and the primary Eval-DB analysis population is important when interpreting who contributed to the endpoint estimates.

The record also illustrates why different statistical summaries should not be conflated. Kaplan-Meier medians and a log-rank test address the time-to-event outcome, while ANCOVA reports a least-squares mean difference for flare-free days. A recalculation from arm summaries can be useful as a check, but it may differ from an adjusted sponsor analysis because the methods answer the comparison using different assumptions and information.

Finally, the breadth of secondary outcomes highlights the importance of multiplicity and outcome-specific interpretation. Measures of flare timing, flare duration, itch, disease severity, and quality of life capture related but distinct constructs. Without a reported adjustment or testing hierarchy, nominal secondary results should not be treated as a collection of independent confirmatory findings. The registry record supports careful reading of the primary comparison while making clear where statistical planning and missing-data details remain unavailable.

15. 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 primary endpoint is restricted to the Eval-DB population of randomized responders meeting the stated ISGA and EASI50 criteria. This is appropriate to the maintenance question described, but it means the result does not directly represent participants who did not meet those criteria. The primary analysis group counts are smaller than the overall enrollment, and the registry does not report a detailed flow of participants through the earlier treatment and randomization stages.

The record provides Kaplan-Meier medians, confidence intervals, and a log-rank p-value, but does not report a hazard ratio for the primary comparison. This limits the available relative-effect description. The median confidence intervals are broad, so the estimated timing is imprecise, particularly for the crisaborole arm. The record does not provide enough detail to assess proportional-hazards assumptions or other sensitivity analyses.

Censoring rules are described, but the numbers and reasons for censoring by arm are not reported in the registry record. The record also does not report a detailed strategy for other missing data, the assessment of informative censoring, or sensitivity analyses. These gaps make it difficult to judge how robust the time-to-event results are to alternative assumptions about participants whose follow-up ended before a first flare.

The registry lists many secondary outcomes, but does not report a multiplicity strategy or a testing hierarchy. This limits the confirmatory interpretation of nominal secondary findings. Some recalculated secondary comparisons use posted summary statistics and are not adjusted analyses; they can differ from the sponsor’s model-based results. The sponsor’s detailed model specifications and covariate adjustments are not reported in the registry record.

The sample-size illustrations are based on observed effects and stated general assumptions, rather than a reported protocol justification. The registry does not provide the original design calculation, interim-analysis plan, or stopping rules. Finally, the safety counts are descriptive, and the record does not supply statistical comparisons that would support causal or comparative safety conclusions.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: A Study to Evaluate Long-Term Maintenance Treatment With Once Daily Crisaborole Ointment 2% in Pediatric and Adult Participants With Mild-to-Moderate Atopic Dermatitis — NCT04040192.
• Registry record last updated 2023-03-08; status last verified 2023-02.
• Results first posted 2023-03-08.
• 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.

19. Record Summary

NCT04040192 is a completed phase 3 randomized, double-blind, vehicle-controlled study sponsored by Pfizer. It evaluated once-daily crisaborole ointment, 2%, as maintenance treatment in pediatric and adult participants aged 3 months and older with mild-to-moderate atopic dermatitis who responded to twice-daily crisaborole.

The primary outcome was duration of flare-free maintenance until the first flare during the double-blind period, analyzed using Kaplan-Meier estimation and a log-rank comparison. The registry reports median estimates of 30 days for vehicle and 111 days for once-daily crisaborole, with a log-rank p-value of 0.003. The primary analysis population was responder-defined.

Secondary outcomes included flare-free days, flare counts and duration, itch response, disease severity, and quality of life. The record does not report a multiplicity strategy, a primary hazard ratio, or a detailed missing-data sensitivity analysis. Safety counts are descriptive and should be interpreted in light of the different study groups and periods represented.