Promiseb Topical Cream for Cradle Cap: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Promiseb Topical Cream for Cradle Cap (NCT01214434), a randomized phase 4 study. The primary outcome is Subjects With Investigator Global Assessment (IGA) Success (IGA of 0 or 1) at End of Treatment (Day 7 or 14)..

2. Clinical Question

This question concerns a binary outcome: each analyzed participant either met the success definition or did not. The resulting group percentages describe the proportion classified as successful at the end of treatment. They do not, by themselves, indicate how much an individual participant’s condition changed, nor do they establish that any observed group difference is precise or attributable to the intervention.

The secondary outcomes address reductions from baseline in scaling, crusting, erythema and oiliness. These measures provide additional descriptions of skin findings, but they are distinct from the primary success definition. The registry record does not report a single combined score covering all of these features.

3. Trial Design

The registry identifies this as a randomized, quadruple-masked, parallel-group pilot study, with a Phase 4 designation and enrollment of 42. The groups compared Promiseb Topical Cream with bland emollient. The official title describes twice-daily cream use and a double-blind, placebo-controlled study; the brief summary says the study evaluated efficacy and safety in cradle cap. The registry status is completed.

The study began in 2010-03, and primary completion was recorded as 2011-06. The registry lists the sponsor as Promius Pharma, LLC. The intervention records classify Promiseb Topical Cream as a device and bland emollient as other. More detailed arm instructions are not reported in the registry record.

The primary outcome was assessed at end of treatment, which could be Day 7 or 14. Thus, the endpoint description allows more than one treatment-end day. The record does not state how the choice of end-of-treatment day was made or whether it was the same across participants.

The posted primary arm summaries include 13 participants for bland emollient and 25 for Promiseb Topical Cream. The primary analysis description says participants with data after baseline were included, while also noting exclusions in both groups and inclusion of one non-completer using Day 7 data carried forward. Further detail on randomization procedures, allocation concealment, masking roles, recruitment criteria, or reasons for the analysis exclusions is not reported in the registry record. Nor is the trial’s original sample-size justification reported. The pilot designation and the observed group sizes therefore should not be mistaken for evidence about the intended precision or statistical power of the original design.

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: All subjects will data after baseline were included in the analysis. For the Bland emollient group, 2 subjects were excluded from the analysis. For the Promiseb group, 3 subjects were excluded and one of the subjects that did not complete the study was included with Day 7 data carried forward to impute missing Day 14 data.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Subjects With Investigator Global Assessment (IGA) Success (IGA of 0 or 1) at End of Treatment (Day 7 or 14)., measured over end of treatment (Day 7 or 14).

The primary endpoint is the percentage of participants judged to have investigator global assessment success at end of treatment, on Day 7 or 14. Success means an IGA score of 0 or 1. The score ranges from 0, clear, to 4, severe, so the endpoint groups the two lowest score categories into a binary outcome: success or no success.

This kind of endpoint is useful because it translates an ordered clinical rating into a clear proportion that can be compared between groups. It describes how often participants reached the specified threshold, rather than the average change in their scores. That makes the endpoint straightforward to interpret, but it also discards some information: participants with scores of 2, 3 or 4 all count as not successful, despite potentially differing severity. The registry record does not report the rationale for choosing the threshold or whether it was prespecified in the protocol.

The posted percentages are 91.7% for bland emollient and 96.0% for Promiseb Topical Cream. These are high success proportions in both groups. The comparison between them, rather than either percentage alone, is the relevant quantity for assessing how the groups differed on the endpoint. The estimate of that difference is imprecise, as its confidence interval includes both a difference favoring bland emollient and a difference favoring Promiseb.

7. Results Posted in the Registry

• Promiseb Topical Cream: 96.0% (24/25) versus 92.3% (12/13) on control; risk difference 3.7 percentage points (95% CI -12.7 to 20.1), risk ratio 1.04 (0.87–1.24); unadjusted two-proportion z-test p = 0.629.

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.

Precent Reduction From Baseline for Scaling at End of Treatment.

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Promiseb Topical Cream: mean 90.00 versus 58.00 on control; difference 32.00 (95% CI -4.12 to 68.12), standardized effect d = 0.82; z-test p = 0.083.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Promiseb Topical Cream and the control. The interval gives the range of effects that remain compatible with the data.

Percent Reduction From Baseline for Crusting at End of Treatment.

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Promiseb Topical Cream: mean 78.00 versus 85.00 on control; difference -7.00 (95% CI -29.56 to 15.56), standardized effect d = -0.17; z-test p = 0.543.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Promiseb Topical Cream and the control. The interval gives the range of effects that remain compatible with the data.

Percent Reduction From Baseline for Erythema at End of Treatment.

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Promiseb Topical Cream: mean 89.00 versus 74.00 on control; difference 15.00 (95% CI -11.38 to 41.38), standardized effect d = 0.46; z-test p = 0.265.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Promiseb Topical Cream and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover changes from baseline in scaling, crusting and erythema; oiliness is listed, but its result is not reported in the registry record. Across the available outcomes, the observed pattern is not uniform: the estimated direction and size differ across measures, and the uncertainty varies. This mixture is a reason to avoid treating any single secondary measure as a complete account of the study findings.

The primary endpoint is a binary investigator judgment at end of treatment, whereas the secondary outcomes are percentage reductions from baseline in specific skin signs. They capture related but different aspects of the assessment. Agreement across them might have offered a broader pattern, but the posted results do not establish one consistent direction across all available measures. The primary comparison remains the central result because it is the designated primary endpoint.

Secondary results are generally less conclusive when several outcomes are examined. In general, testing many outcomes creates more opportunities for a nominally small p-value to arise by chance, especially if no adjustment or prespecified hierarchy is used. The registry record does not report a multiplicity adjustment, a formal hierarchy among secondary outcomes, or an analysis plan that indicates how these results were intended to be interpreted.

The sponsor’s reported p-values and the simple unadjusted recalculations do not always match. The recalculations are useful for examining the posted summary statistics, but they should not be used to select whichever result appears more favorable. The sponsor’s own analysis takes precedence where results differ. Taken together, the secondary outcomes are best read as exploratory descriptions that add context to the primary result, not as independent confirmation of a definitive effect.

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

• Precent Reduction From Baseline for Scaling at End of Treatment.
• Percent Reduction From Baseline for Crusting at End of Treatment.
• Percent Reduction From Baseline for Erythema at End of Treatment.
• Percent Reduction From Baseline for Oiliness at End of Treatment.

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary percentage represent?

The primary outcome is binary. Each participant included in the analysis is classified as having IGA success or not having success, using a score of 0 or 1 as the threshold. A group percentage is the proportion meeting that definition. This is different from a mean score: the percentage does not retain the distinctions among scores outside the success range.

For a binary outcome, a risk difference expresses the difference between the groups’ success proportions. The recalculated estimate is 0.037 for Promiseb compared with bland emollient. A value of zero would mean the estimated proportions were the same; positive values indicate a higher estimated proportion in the Promiseb group, while negative values indicate a higher estimated proportion in the bland emollient group. The confidence interval spans both signs, so the direction and size of the underlying difference remain uncertain.

Why does the analysis method matter?

The registry reports a chi-squared analysis for the primary comparison. In general, a chi-squared test assesses whether categorical outcome proportions differ across groups under its assumptions. The recalculation uses the posted counts and group sizes to produce an unadjusted estimate and interval for the risk difference, along with an unadjusted p-value. These procedures need not return identical results, particularly when the analysis population or details of the method differ. The registry record does not report further specifications of the sponsor’s chi-squared analysis.

For continuous outcomes, the sponsor reports two-sided t-tests. In general, a t-test compares group means while accounting for variability and sample size. The posted secondary results also include mean differences and confidence intervals recalculated from the group means, standard deviations and sample sizes. These are simple, unadjusted recalculations from summary statistics. They do not reproduce every possible detail of the sponsor’s original analysis.

What is a p-value?

In general, a p-value describes how incompatible the observed data are with a specified null hypothesis, under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of a difference. A value above a conventional significance threshold does not establish that the groups are equivalent; it can also reflect limited information or considerable variability. The registry record does not report the prespecified significance threshold for the original trial analysis.

The sponsor reports the primary p-value as >0.05. The recalculated primary p-value is 0.629. Both indicate that the reported primary analysis did not meet the conventional 0.05 threshold, but the p-value alone does not tell how large a difference is compatible with the data. For scaling, the sponsor’s reported p-value is =0.03, while the recalculated unadjusted value is 0.083. In that instance, the methods or analysis details behind the difference are not fully reported, and the sponsor’s result takes precedence.

Why is over-dispersion relevant in general?

For a binary endpoint, a basic binomial model treats each participant’s outcome as a binary event and assumes that variability is adequately represented by the event probability and sample size. In general, over-dispersion means that observed variability is greater than such a model expects. It can make uncertainty estimates too narrow if ignored. The registry record does not report an over-dispersion assessment, a model-based adjustment, or enough information to determine whether this issue was examined. No claim about over-dispersion can be made from the posted summaries alone.

What does the endpoint timing imply?

The primary assessment is recorded at end of treatment, Day 7 or 14. In general, variation in assessment timing can matter if outcomes change over time. The registry does not report how the two assessment days were assigned or whether timing was incorporated into the analysis. The posted estimate should therefore be understood as the comparison for the endpoint as defined in the record, not as a single fixed-day estimate.

How should the analysis population be read?

The primary description says participants with data after baseline were included, and notes that 2 participants in the bland emollient group and 3 in the Promiseb group were excluded. It also says one participant who did not complete the study was included using Day 7 data carried forward. This means the posted result is not simply described as an analysis of every enrolled participant with all outcomes observed at the same time. The reasons for exclusions, the handling of other missing observations, and the full analysis-population definition are not reported in the registry record.

Carrying an earlier observation forward is a missing-data procedure. In general, such procedures rely on assumptions about how the outcome would have changed after the last recorded observation. Carry-forward does not recover the unobserved outcome; it substitutes an earlier value according to a rule. The registry description does not provide enough detail to assess the assumptions or sensitivity of the primary result to this handling.

These methods descriptions distinguish the registry’s reported analyses from simple recalculations and general statistical concepts. The recalculated comparisons are not adjusted for multiple outcomes or other covariates. The record does not report whether the sponsor used adjustments or additional analyses beyond those listed.

11. Confidence Intervals and Precision

A confidence interval describes a range of values reasonably compatible with the observed data under the method used. It conveys uncertainty about the estimate, rather than guaranteeing that the true value lies inside the interval. A wide interval indicates that the data do not pin down the group difference closely.

For primary success, the recalculated risk difference is 0.037, and its 95% confidence interval runs from -0.127 to 0.201. Because the interval crosses zero, the data are compatible with no group difference as well as with differences in either direction. Its breadth is important: the observed point estimate is not precise enough to distinguish a small difference from a materially different one on the risk-difference scale. No equivalence or non-inferiority margin is reported in the registry record, so the interval cannot be judged against such a prespecified clinical boundary.

For the secondary continuous outcomes with recalculated intervals, the intervals also span zero. In general, a confidence interval that spans zero for a mean difference leaves uncertainty about both direction and size. The intervals are not substitutes for the sponsor’s reported analyses, and the registry does not provide sponsor confidence limits for these comparisons.

Precision depends on the amount of information and the variability in the data. In general, small groups and variable outcomes tend to yield less precise estimates. The posted primary groups contain 13 and 25 participants, and the secondary analyses have their own reported group sizes. A pilot study of this size can produce informative estimates, but the uncertainty should remain prominent when interpreting them. Confidence intervals describe statistical precision under the analysis method; they do not address every potential source of bias, such as missing-data decisions, endpoint timing, or limitations in the registry description.

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 planning figures are participants per arm, not total events. They are illustrations based on the observed effect and are not the trial’s original sample-size calculation. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set at the stated fraction of the observed effect. The trial’s original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a design with an 80% chance of detecting the assumed effect if that effect were the true one, under the stated assumptions and analysis framework. The 90% power column gives the corresponding illustration for a 90% chance. These are planning concepts: higher power generally requires more information, all else being equal.

The rows use different fractions of the observed effect as the target. Planning for 75% of the observed effect means assuming a smaller target difference than planning for 100%; planning for 50% assumes a still smaller target. Smaller effects need more participants to distinguish them from random variation at a given significance level and power. The displayed figures can therefore rise sharply as the target effect gets smaller.

These figures are not observed power. They do not state the probability that this completed trial detected a true effect, and they cannot turn the observed results into a reliable estimate of efficacy. They are hypothetical planning illustrations derived from the posted effect estimates, which themselves may be unstable in a pilot study.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.923; treatment proportion p₁ = 0.960; average p̄ = 0.942.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3318 = 0.6503.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3308 = 0.2784.
4. n = (0.6503 + 0.2784)² / (0.0369)² = 632.6, rounded up to 633 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 <- 0.923076923076923                          # control proportion
p1 <- 0.96                          # 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(1214434)
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 = 633 (80% power), 847 (90% power)
 75% of observed effect: n per arm = 1,209 (80% power), 1,618 (90% power)
 50% of observed effect: n per arm = 2,906 (80% power), 3,890 (90% power)
power.prop.test: 632.6 
Simulated power at n = 633 per arm: 0.808 (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.

14. Analyses Reported by the Sponsor

The registry reports a chi-squared test for the primary comparison, with p >0.05. The unadjusted recalculation from the posted primary summary statistics gives a risk difference of 0.037, a 95% confidence interval from -0.127 to 0.201, and p = 0.629. Both the reported result and recalculation indicate that the primary comparison did not meet the conventional 0.05 significance threshold. The recalculation adds an interval for the difference but does not replace the sponsor’s analysis.

For the secondary outcomes, the sponsor reports two-sided t-tests. For scaling, the sponsor’s p-value is =0.03, whereas the recalculated unadjusted p-value is 0.083. The reported and recalculated p-values also differ for crusting and erythema. The registry does not provide enough detail to determine the precise reasons for these differences, such as any analysis specifications not captured in the posted summaries.

The simple recalculations are based on posted summary statistics and are unadjusted. They may not reproduce the sponsor’s analysis population, assumptions, or implementation in full. Where the sponsor’s own analysis differs from a simple recalculation, the sponsor’s own analysis takes precedence. The registry record does not report additional detail that would support reconciling every difference.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes. The primary endpoint is investigator global assessment success. Secondary endpoints include reductions from baseline in scaling, crusting, erythema and oiliness, although a result for oiliness is not reported in the registry record. The record does not state whether a formal testing hierarchy was used or whether statistical significance for secondary outcomes was adjusted for the number of comparisons.

Multiplicity matters in general because each additional statistical test creates another opportunity for a chance finding. If multiple outcomes are examined without adjustment, a single small p-value may be less persuasive than it would be as the only planned test. The reported secondary p-values should therefore be interpreted cautiously. The registry record does not report a family-wise error strategy, a false-discovery approach, or another multiplicity method.

The analysis population is described as including subjects with data after baseline. The record also notes that 2 bland-emollient participants and 3 Promiseb participants were excluded from the primary analysis, and that one participant who did not complete the study was included using Day 7 data carried forward. The reasons for the exclusions are not reported in the registry record. The wording does not provide a full account of missing observations or clearly establish how every participant was handled for every endpoint.

In general, missing-data methods require assumptions about outcomes that were not observed. Carrying an earlier result forward is one such approach, but the registry does not report the rationale for its use, whether other approaches were considered, or whether sensitivity analyses were conducted. The record also does not report the original protocol’s statistical analysis plan, details of any interim analyses, or the trial’s sample-size justification. These omissions limit assessment of whether the posted analyses match the original plans and how robust the findings are to alternative analysis choices.

16. 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 non-serious adverse event terms

The registry lists serious adverse events among 12 participants at risk in the bland emollient group and 25 in the Promiseb group; no serious adverse events are recorded as affecting participants in either group. The registry also lists other adverse events among 12 bland-emollient participants at risk, with 1 affected, and among 25 Promiseb participants at risk, with 0 affected. Death counts are not reported in the registry record.

These counts describe the safety information posted for the listed groups. They should be read with the number at risk and with the limited size of the study in mind. In general, observing no serious events in a study does not establish that an event cannot occur or that two interventions have the same safety profile. The record does not provide detailed event terms for the one other adverse event, and no serious adverse event terms are listed.

The registry’s safety group sizes differ from the primary analysis group summaries. The record does not explain the difference in denominators, so these figures should not be assumed to use the same analysis population as the efficacy endpoint. Further detail about adverse-event collection, severity, relatedness, or follow-up is not reported in the registry record.

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

The results show high posted primary success proportions in both groups: 91.7% with bland emollient and 96.0% with Promiseb. The recalculated comparison is uncertain, with a 95% confidence interval that includes zero and values in either direction. The sponsor’s reported primary test likewise has p >0.05. These findings describe the posted data; they do not establish that the groups are equivalent, nor do they establish a clear difference.

A non-significant result is not proof that there is no effect. In general, it can arise when the true difference is small, when data are variable, or when the study provides limited precision. Conversely, the numerical difference between the posted percentages does not by itself establish a real or meaningful advantage. The confidence interval is central because it shows that the estimate remains compatible with a range of possible differences.

The secondary findings offer additional descriptions of scaling, crusting and erythema, but they do not provide a consistent basis for replacing or overriding the primary result. The oiliness outcome has no posted result. The secondary analyses also carry added uncertainty because the registry record does not report multiplicity adjustment or a hierarchy for these outcomes.

The study is described as a pilot and includes a relatively small number of analyzed participants in the primary group summaries. Its results can be useful for describing the observed outcomes and the uncertainty that remains, but the planning illustrations based on observed effects should not be mistaken for the original study design or for evidence of observed power.

Interpretation is also limited by the analysis-population description, exclusions, carried-forward Day 7 observation, and the endpoint timing of Day 7 or 14. Details needed to judge these choices fully are not reported in the registry record. The findings apply to the outcomes and participants described in this record and do not provide information about longer-term outcomes, populations beyond those studied, or other endpoints that were not posted.

18. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between a group percentage and a precise comparison. The posted success proportions are high in both groups, but the relevant estimate is the difference between them, with its uncertainty. The primary confidence interval spans zero and both directions, so the observed numerical ordering is not enough to determine which group had the higher underlying success proportion.

The study also shows why p-values and confidence intervals should be read together. The sponsor’s primary test is reported as p >0.05, while the recalculated comparison supplies a risk-difference interval. Neither a non-significant p-value nor a point estimate alone answers how large a difference remains compatible with the data. Precision is an essential part of interpretation.

The secondary findings demonstrate another common issue: multiple outcomes can produce a varied pattern, and isolated p-values are harder to interpret when the multiplicity plan is unknown. Here, a sponsor-reported secondary p-value differs from a recalculated one, underscoring that a summary-statistic recalculation is not the same as reproducing a full analysis. The registry’s missing detail on analysis plans and missing data limits what can be concluded about those differences.

Finally, the sample-size illustrations clarify the distinction between planning and evaluation. Figures based on observed effects can illustrate how smaller target effects require more participants, but they are not evidence of the trial’s original design rationale or its observed power. This distinction is especially important when interpreting pilot results, where estimates may be imprecise and should be treated as descriptive evidence rather than definitive answers.

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

Several trial-specific limitations affect interpretation. The enrollment is 42, while the posted primary analysis summaries include 13 bland-emollient participants and 25 Promiseb participants. The analysis description notes exclusions in both groups, but the reasons for those exclusions are not reported in the registry record. The record does not fully explain how the analysis population was defined for all outcomes.

The primary assessment could occur at Day 7 or 14. The registry does not report how the assessment day was determined, whether the timing varied systematically, or how timing was handled analytically. One non-completer was included with Day 7 data carried forward, but the rationale for that procedure and sensitivity to other missing-data assumptions are not reported.

The primary confidence interval is broad, leaving uncertainty about the direction and magnitude of the group difference. The trial’s original sample-size justification is not reported; the planning illustrations derived from the observed effect cannot fill that gap. The record does not report detailed randomization procedures, allocation concealment, masking implementation, the original statistical analysis plan, or interim analyses.

The registry also does not report a multiplicity strategy for the secondary outcomes, and oiliness has no posted result. For scaling, the sponsor’s reported p-value differs from the unadjusted recalculation. The record lacks detail needed to reconcile the difference. Finally, the safety summaries provide limited information about the other adverse event and do not report death counts. These limitations constrain assessment of both efficacy and safety from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Promiseb Topical Cream for Cradle Cap — NCT01214434.
• Registry record last updated 2017-03-07; status last verified 2017-01.
• Results first posted 2013-11-20.
• 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

The registry describes a completed randomized, quadruple-masked, parallel-group pilot study of Promiseb Topical Cream versus bland emollient in pediatric subjects with cradle cap. Enrollment was 42. The primary endpoint was investigator global assessment success, defined as a score of 0 or 1 at end of treatment on Day 7 or 14.

Posted primary success proportions were 91.7% for bland emollient and 96.0% for Promiseb. The sponsor reports a chi-squared result of p >0.05. The unadjusted recalculation gives a risk difference of 0.037, with a 95% confidence interval from -0.127 to 0.201. Secondary results are available for scaling, crusting and erythema; oiliness results are not reported in the registry record.

The primary comparison is imprecise, and analysis details are limited. The registry record does not report the original sample-size justification, full statistical analysis plan, multiplicity strategy, or complete reasons for exclusions. The sponsor’s own analysis takes precedence when it differs from an unadjusted recalculation.