Phase III Efficacy and Safety Study of Oleogel-S10 in Epidermolysis Bullosa: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase III Efficacy and Safety Study of Oleogel-S10 in Epidermolysis Bullosa (NCT03068780), a randomized phase 3 study. The primary outcome is Proportion of Patients With First Complete Closure of the EB Target Wound Within 45 Days of Treatment.

2. Clinical Question

3. Trial Design

This was a Phase III, randomized, parallel-group, triple-masked study of Oleogel-S10 versus control gel in people with inherited epidermolysis bullosa. The registry lists enrollment of 223 participants and a completed status. The listed start date is 2017-03-29 and primary completion date is 2020-06-11. The official title describes a double-blind treatment phase followed by a 24-month open-label follow-up.

The main comparison used a vehicle control intended to resemble Oleogel-S10 in appearance and texture. The registry summary says packaging was identical and describes a 90-day double-blind phase. The stated randomization probability of receiving Oleogel-S10 was 50%. The primary outcome was assessed within 45±7 days, whereas a number of secondary outcomes were assessed at 90±7 days or by the end of the double-blind phase.

The overall registry enrollment and the primary endpoint analysis populations are not interchangeable quantities. For the primary endpoint, the posted group counts are 109 for Oleogel-S10 and 114 for control gel; the endpoint population is identified as the Full Analysis Set. Other outcomes have their own posted analysis counts, which differ by outcome. The registry record does not report the original sample-size justification, the planned interim analyses, or a complete statistical analysis plan. The reported design characteristics therefore establish the broad comparison and masking, but do not establish every operational or analytical detail.

The record also includes an open-label follow-up and safety results labeled as former Oleogel-S10 and former control gel groups. These follow-up categories should be distinguished from the double-blind randomized comparison when reading the results. The reported follow-up groups are not presented as a continuing blinded comparison.

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: All subjects satisfied the inclusion / exclusion criteria based on investigator assessment prior to entry into the study. 29 out of a total of 252 screened patients were reported as screen failures.

Double-Blind Phase (DBP)

Open-Label Phase (OLP)

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS)

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 Proportion of Patients With First Complete Closure of the EB Target Wound Within 45 Days of Treatment, measured over 45±7 days.

The primary endpoint is the proportion of participants whose EB target wound had its first complete closure within 45 days of treatment, with the assessment window stated as 45±7 days. The target was a partial-thickness wound of 10 cm2 to 50 cm2, present for at least 21 days but less than 9 months, in a participant with inherited EB subtypes DEB, JEB or Kindler EB. Closure meant the first investigator assessment at which complete re-epithelialization was present without drainage.

This binary endpoint records whether each participant met the closure criterion within the specified period, rather than measuring the amount of change in wound size. Comparing the proportions in the randomized groups addresses whether the observed frequency of this event differed between Oleogel-S10 and control gel during the early assessment window. It is clinically interpretable as an event count, while the time limit makes the question specific to relatively early wound closure rather than eventual closure over longer follow-up.

General statistical context: a binary endpoint can be summarized as an event count and a group proportion, with a contrast such as a risk difference or odds ratio. These contrasts describe different scales of comparison and need not have numerically matching values. The investigator’s clinical assessment is integral to the recorded endpoint; the registry definition does not describe an independent adjudication procedure.

7. Results Posted in the Registry

• Oleogel-S10: 41.3% (45/109) versus 28.9% (33/114) on control; risk difference 12.3 percentage points (95% CI -0.1 to 24.8), risk ratio 1.43 (0.99–2.05); unadjusted two-proportion z-test p = 0.053.

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.

Proportion of Patients With First Complete Closure of the EB Target Wound at D90 or EDBP Based on Clinical Assessment by the Investigator Until D90 or EDBP

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Oleogel-S10: 50.5% (55/109) versus 43.9% (50/114) on control; risk difference 6.6 percentage points (95% CI -6.5 to 19.7), risk ratio 1.15 (0.87–1.52); unadjusted two-proportion z-test p = 0.324.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oleogel-S10 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline (DBP D0) in Total Body Wound Burden as Evidenced by Clinical Assessment Using Section I (Assessment of the Skin Except for the Anogenital Region) of the 'EB Disease Activity and Scarring Index' (EBDASI), at D90 or EDBP

• 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 errors.
• Result:
  • Oleogel-S10: mean -0.44 versus -0.56 on control; difference 0.12 (95% CI -2.31 to 2.55), standardized effect d = 0.01; z-test p = 0.923.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oleogel-S10 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline (DBP D0) in Itching Using the 'Itch Man Scale' in Patients ≥ 4 Years and up to 13 Years of Age Before Wound Dressing Changes at D90 or EDBP

• 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:
  • Oleogel-S10: mean -0.44 versus -1.00 on control; difference 0.56 (95% CI -0.01 to 1.13), standardized effect d = 0.43; z-test p = 0.053.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oleogel-S10 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover closure by the end of the double-blind phase, total body wound burden and itching in age-defined groups, as well as other measures listed in the registry. Across the posted numerical results, there is no single uniform pattern: estimates vary by outcome, and the uncertainty intervals for the reported comparisons include values near the corresponding null in several cases. The outcomes also differ in scale, assessment timing and number of participants contributing data, so they do not form one common measure of treatment effect.

These secondary findings provide context around the primary wound-closure question but do not independently settle it. Closure by 90 days is related to the primary endpoint but uses a later assessment window. Wound burden and itching address different aspects of the condition and are measured with separate instruments. A result on one of these outcomes cannot be assumed to confirm or contradict the primary endpoint without considering what was measured and when.

The registry reports several secondary outcomes but does not report a multiplicity adjustment plan. General statistical context: when many outcomes are tested, the chance of at least one apparently notable result can increase, even when no underlying effect is present. Unadjusted secondary p-values should therefore carry less weight than a clearly defined primary analysis, especially when the outcome hierarchy and analysis plan are not fully reported. The registry record does not report the statistical plan needed to determine whether any secondary endpoints were prespecified as confirmatory.

There are seven posted secondary outcomes, while the available numerical summaries shown in the record cover only some of them. For outcomes without numerical results in the registry entries, the results are not reported in the registry record. The breadth of measured outcomes is useful for describing the study’s scope, but it does not remove uncertainty about the primary result or establish effects across all domains.

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

• Time to First Complete Closure of the EB Target Wound as Evidenced by Clinical Assessment Until Day 90 (D90) or End of Double-blind Phase (EDBP)
• Proportion of Patients With First Complete Closure of the EB Target Wound at D90 or EDBP Based on Clinical Assessment by the Investigator Until D90 or EDBP
• The Incidence of EB Target Wound Infection Between Baseline (DBP D0) and D90 or EDBP as Evidenced by Adverse Events (AEs) and/or Use of Topical and/or Systemic Antibiotics (Related to Wound Infection)
• The Maximum Severity of EB Target Wound Infection Between Baseline (DBP D0) and D90 or EDBP as Evidenced by AEs
• Change From Baseline (DBP D0) in Total Body Wound Burden as Evidenced by Clinical Assessment Using Section I (Assessment of the Skin Except for the Anogenital Region) of the 'EB Disease Activity and Scarring Index' (EBDASI), at D90 or EDBP
• Change From Baseline (DBP D0) in Itching Using the 'Itch Man Scale' in Patients ≥ 4 Years and up to 13 Years of Age Before Wound Dressing Changes at D90 or EDBP
• Change From Baseline (DBP D0) in Itching Using the 'Leuven Itch Scale' in Patients ≥ 14 Years of Age Before Wound Dressing Changes at D90 or End of Double Blind Phase (EDBP)

9. Statistical Interpretation

10. Statistical Methods Explained

General statistical context: randomized assignment aims to make treatment groups comparable at the start of a trial, so that an outcome contrast can be interpreted as a comparison of assigned groups. Randomization does not guarantee identical groups in every feature, particularly in a trial of this size, and it does not eliminate issues arising from outcome definitions, missing observations or analysis choices. The registry identifies this study as randomized and parallel-group, but the allocation sequence method and concealment details are not reported in the registry record.

What does the primary contrast represent?

The posted primary outcome is binary: each participant either had first complete target-wound closure within the defined period or did not. The event counts are 45 among 109 in the Oleogel-S10 group and 33 among 114 in the control group. The recalculation expresses the comparison as a risk difference, which is the difference between the two group proportions on an absolute scale. A positive estimate in this comparison means the observed event proportion was higher in the Oleogel-S10 group. The recalculated risk difference is 0.123.

Other common summaries for binary outcomes use relative scales. An odds ratio compares the odds of the event between groups; a risk ratio compares the event proportions. These measures answer related but distinct questions and their numerical values are not directly interchangeable with a risk difference. The registry’s sponsor analysis uses an odds ratio, while the simple recalculation reports a risk difference. Because the registry marks a discrepancy between the analyses, the sponsor’s own result takes precedence for the trial’s reported analysis.

Why can analyses of the same endpoint differ?

General statistical context: methods can differ in their model, adjustment, handling of the analysis population, assumptions and calculation of uncertainty. For binary outcomes, choices about stratification or other design features can affect an odds-ratio estimate and its standard error. A simple calculation from counts is deliberately unadjusted and does not reproduce methods that require participant-level data or additional trial details. The registry names the Cui, Hung, Wang approach for the reported odds ratio, but the details needed to recreate that analysis are not reported in the registry record. The difference between its result and the unadjusted recalculation should therefore be acknowledged without attributing it to a specific cause.

What does the confidence interval communicate?

General statistical context: a confidence interval describes the range of estimates compatible with the data and the method used, subject to the method’s assumptions. A broad interval indicates that the effect is not precisely determined. For the recalculated risk difference, the 95% interval runs from -0.001 to 0.248, spanning values close to no difference as well as larger positive differences. The sponsor-reported odds-ratio interval runs from 1.02 to 3.30. These intervals are on different scales and arise from different analyses, so they should not be compared by their raw numerical widths.

A p-value measures how unusual the observed data, or more extreme data, would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, nor a measure of clinical importance. The recalculated p-value is 0.053; the sponsor-reported p-value is 0.013. Because these values accompany different analyses and the registry flags a discrepancy, they should not be blended into a single result.

How should continuous outcomes be read?

Some secondary endpoints are continuous scores, including wound burden and itching. A group mean or least-squares mean describes an average score or change, while a standard deviation or standard error describes a different aspect of variability. General statistical context: the standard deviation describes spread among individual observations, whereas the standard error describes the uncertainty of an estimated mean. The registry lists standard errors for the wound-burden least-squares means and standard deviations for the child itching means. That distinction matters when interpreting the precision of the group summaries.

For wound burden, the comparison is a mean difference of 0.12 with a 95% confidence interval from -2.306 to 2.546 and an unadjusted p-value of 0.923. The reported estimate is small relative to the interval’s range, which includes values on either side of no difference. For the Itch Man Scale, the mean difference is 0.56, with a 95% interval from -0.008 to 1.128 and an unadjusted p-value of 0.053. These results should be understood in the context of their specific score scales, available outcome counts and lack of multiplicity adjustment reported in the registry record.

Why does over-dispersion matter?

General statistical context: over-dispersion occurs when observed variability is greater than a model assumes. When that happens, standard errors can be too small if the model does not account for the extra variability, making confidence intervals too narrow and p-values too small. The registry does not report a dispersion parameter for the primary binary outcome, and the sponsor method cannot be reconstructed from the posted summary. Over-dispersion is therefore a general consideration rather than a documented feature of this analysis.

The registry record identifies the primary analysis population as the Full Analysis Set, but it does not report the detailed analysis rules, missing-data handling or complete model specification. Those omissions limit independent reproduction of the sponsor analysis. The simple recalculation is a useful summary-statistic check, but it does not supply those missing details or supersede the sponsor’s reported method.

11. Confidence Intervals and Precision

The sponsor-reported primary odds ratio is 1.84, with a 95% confidence interval from 1.02 to 3.30. The interval lies above 1, the no-association value for an odds ratio, but extends to a range of estimates substantially larger than its lower bound. This conveys uncertainty about the size of the association even though the sponsor-reported p-value is 0.013.

The unadjusted recalculation uses a different scale. Its risk difference is 0.123, with a 95% confidence interval from -0.001 to 0.248. The interval includes values very close to no difference and also allows for a larger positive difference. Its unadjusted p-value is 0.053. The contrast between this interval and the sponsor’s interval should not be interpreted as a direct precision comparison: one is a risk difference and the other is an odds ratio, and the analyses differ.

General statistical context: a confidence interval is not a guarantee that the true effect lies within its endpoints. It is a method-based range that reflects sampling uncertainty under the analysis assumptions. Precision depends on the amount of information and variability, not only on the point estimate. A wide interval leaves substantial uncertainty about effect size, while an interval close to the null value can indicate that the data are compatible with little or no difference as well as some degree of effect.

Several secondary estimates also have intervals that cross their respective null values. The outcome-specific estimates and intervals should be interpreted on their own scales, with attention to their different sample counts. The registry does not report enough details to quantify how missing data or other modeling decisions affect these intervals.

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

For the primary endpoint, planning for 100% of the observed effect gives 234 participants per arm for 80% power and 313 participants per arm for 90% power. Planning for 75% of the observed effect gives 408 participants per arm for 80% power and 546 participants per arm for 90% power. Planning for 50% of the observed effect gives 897 participants per arm for 80% power and 1,201 participants per arm for 90% power. The corresponding secondary-outcome planning values are specific to each outcome and its observed effect.

In plain language, 80% power means that, if the assumed effect and planning assumptions were correct, a study of the stated size would have an 80% chance of detecting an effect at the specified significance level. The 90% column describes a higher chance of detection under those same assumptions, and therefore requires more participants. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants. These figures are planning illustrations and are not observed power.

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 = 0.289; treatment proportion p₁ = 0.413; average p̄ = 0.351.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6751 = 1.3231.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6694 = 0.5634.
4. n = (1.3231 + 0.5634)² / (0.1234)² = 233.8, rounded up to 234 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 <- 0.289473684210526                          # control proportion
p1 <- 0.412844036697248                          # 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(3068780)
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 = 234 (80% power), 313 (90% power)
 75% of observed effect: n per arm = 408 (80% power), 546 (90% power)
 50% of observed effect: n per arm = 897 (80% power), 1,201 (90% power)
power.prop.test: 233.8 
Simulated power at n = 234 per arm: 0.797 (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 the sponsor’s primary analysis as an odds ratio of 1.84 using the Cui, Hung, Wang approach, with a 95% confidence interval from 1.02 to 3.30 and p = 0.013. The simple recalculation from posted counts instead gives a risk difference of 0.123, a 95% confidence interval from -0.001 to 0.248, and an unadjusted p-value of 0.053.

These are not identical estimates or tests: the sponsor reports an odds ratio, while the recalculation is an unadjusted comparison of proportions on the risk-difference scale. The registry flags a discrepancy. Accordingly, the sponsor’s own analysis takes precedence as the reported trial analysis; the recalculation is best treated as a transparent check of the posted event counts, not as a replacement for the sponsor’s method.

The registry record does not report enough detail to reproduce the Cui, Hung, Wang analysis or explain why its result differs from the simple calculation. The reported odds ratio and its interval should therefore be cited as the sponsor’s analysis, with the recalculated result presented separately and its unadjusted nature made clear.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes or analyses are tested, because the chance of at least one result appearing statistically notable can increase as more tests are considered. The registry lists a primary endpoint and multiple secondary outcomes, but a multiplicity adjustment strategy is not reported in the registry record. It is also not reported whether a formal hierarchy or gatekeeping plan determined which outcomes could support confirmatory conclusions. As a result, unadjusted secondary p-values should be interpreted as exploratory or supportive rather than as a collection of independent confirmations.

The primary analysis population is named as the Full Analysis Set. The registry does not report the detailed rules defining this set, such as the handling of participants without an evaluable wound assessment. Missing-data methods, imputation procedures and sensitivity analyses are not reported in the registry record. Those details matter because the endpoint is based on an investigator assessment within a specified time window, and incomplete follow-up could affect which participants contribute to an analysis.

The posted participant counts differ across outcomes. This may reflect outcome-specific availability or analysis populations, but the reasons are not reported in the registry record and should not be inferred. The record does not report a full statistical analysis plan, the original sample-size justification or interim analyses. Without those details, independent assessment of prespecification, analysis choices and protection against selective interpretation is limited.

The sponsor-reported primary result and the unadjusted recalculation also differ. The registry identifies the sponsor method as Cui, Hung, Wang and marks a discrepancy, but does not provide sufficient detail to reproduce it. A clear account of the planned model, covariates, missing-data rules and multiplicity procedures would help readers distinguish planned analyses from additional analyses and understand how uncertainty was handled.

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: oesophageal stenosis (5.7%), anaemia (5.7%), squamous cell carcinoma skin (3.0%), septic shock (2.0%), bacteraemia (2.0%).

During the double-blind phase, serious adverse events were reported for 7 of 109 participants in the Oleogel-S10 group and 6 of 114 in the control gel group. Other adverse events were reported for 89 of 109 and 92 of 114, respectively. No deaths were recorded for either group in this phase. The listed serious-event terms include oesophageal stenosis and anaemia, each reported as 5.7%, as well as squamous cell carcinoma skin at 3.0%, septic shock at 2.0%, bacteraemia at 2.0% and COVID-19 at 2.0%.

For the open-label follow-up categories, serious adverse events were reported for 26 of 100 former Oleogel-S10 participants and 24 of 105 former control gel participants; other adverse events were reported for 77 of 100 and 81 of 105, respectively. Deaths were recorded for 7 and 2 participants in those groups. These follow-up figures describe the posted categories and should not be read as a blinded randomized comparison.

General statistical context: adverse-event counts describe events recorded during specified observation periods. They do not establish causation, and comparisons can be affected by duration of follow-up, exposure and group definitions. The registry record does not provide enough detail to attribute individual events to treatment.

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

The primary endpoint asks a narrow question: whether first complete closure of a defined EB target wound occurred within 45 days, assessed by the investigator, in the Full Analysis Set. The posted event counts are 45 of 109 for Oleogel-S10 and 33 of 114 for control gel. The sponsor’s analysis reports an odds ratio of 1.84 with a 95% confidence interval from 1.02 to 3.30 and p = 0.013. The simple unadjusted recalculation gives a different result, and the registry marks this discrepancy. The sponsor’s own analysis takes precedence as the reported trial analysis.

This finding does not establish that every wound will close, that all people with inherited EB will have the same outcome, or that results apply to conditions outside the enrolled population and wound definition. It also does not answer whether any observed difference persists after the double-blind period. The open-label follow-up has a different design and cannot be treated as an extension of the randomized comparison without qualification.

A statistical result is not a direct measure of clinical importance. The estimate and its confidence interval describe uncertainty on a statistical scale; the registry does not provide a threshold for a clinically important difference. Nor does the primary result establish an effect on every secondary outcome, such as total body wound burden or itching.

The safety counts identify events recorded during the trial phases, but counts alone do not prove that treatment caused an event or establish comparative safety across follow-up categories. The registry record does not report the full analysis plan, detailed missing-data approach or original sample-size justification, limiting the ability to assess all design and analysis choices. The most defensible reading is therefore specific: the registry reports a positive sponsor analysis for the defined primary endpoint, while the simple unadjusted recalculation is less decisive and the available record leaves important analytical details unresolved.

18. Why This Trial Matters Statistically

This trial presents a useful statistical example of why an endpoint definition, analysis scale and analysis method all matter. The primary outcome is a binary clinical assessment with a clear event criterion and an early time window. The posted counts allow a simple unadjusted comparison, while the sponsor’s reported analysis uses a named odds-ratio method. Those analyses produce different inferential results, and the registry flags the discrepancy. Readers therefore need to distinguish a transparent recalculation from the analysis reported by the sponsor rather than treating them as interchangeable.

The confidence intervals also make precision central to interpretation. The recalculated risk-difference interval ranges from -0.001 to 0.248, while the sponsor-reported odds-ratio interval ranges from 1.02 to 3.30. These intervals use different scales and methods, but both remind readers that an estimate is not a complete description of uncertainty. The point estimate alone cannot communicate how widely plausible effects may vary.

The study also illustrates the limits of secondary outcomes when the analysis plan and multiplicity approach are not reported. The outcomes span closure, wound burden and itching, with different measures and analysis counts. They add breadth to the clinical questions, but unadjusted results across multiple endpoints require restraint.

Finally, the safety record distinguishes the double-blind comparison from open-label follow-up groups. Keeping those phases separate is essential when describing event counts. These features make the record relevant for learning how to read randomized trial results without overstating what summary statistics can 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 does not report the complete statistical analysis plan, original sample-size justification, interim analyses, detailed randomization procedures or allocation concealment. It names the Full Analysis Set for the primary outcome but does not report the detailed rules defining that population. The missing-data approach and sensitivity analyses are also not reported in the registry record. These omissions limit independent reproduction and assessment of the sponsor’s analysis.

The registry flags a discrepancy between the sponsor-reported primary analysis and the simple recalculation from the posted counts. The sponsor’s own analysis takes precedence, but the information available does not explain the difference or allow the Cui, Hung, Wang result to be independently reconstructed. The recalculation is unadjusted and should not be mistaken for the sponsor’s model.

The primary outcome depends on investigator assessment of wound closure. The record defines closure as complete re-epithelialization without drainage, but does not report whether assessments were independently adjudicated or how disagreements were handled. The broad triple-masking label is reported, but details about masking procedures and their maintenance are not reported in the registry record.

Secondary outcomes use distinct instruments, timings and analysis counts. A multiplicity strategy is not reported, and many listed secondary outcomes lack posted numerical summaries in the record. Open-label follow-up safety groups are not equivalent to the randomized double-blind groups. These constraints argue for limiting interpretation to the defined outcomes and periods rather than extending findings beyond what the registry reports.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Phase III Efficacy and Safety Study of Oleogel-S10 in Epidermolysis Bullosa — NCT03068780.
• Registry record last updated 2023-07-20; status last verified 2023-07.
• Results first posted 2023-07-03.
• 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 NCT03068780 as a completed, randomized, parallel-group Phase III study of Oleogel-S10 versus control gel in inherited epidermolysis bullosa. It lists enrollment of 223 participants and a 90-day double-blind phase, followed by an open-label follow-up. The primary endpoint was first complete closure of an EB target wound within 45 days, assessed by the investigator.

The sponsor-reported primary analysis is an odds ratio of 1.84, with a 95% confidence interval from 1.02 to 3.30 and p = 0.013. A simple unadjusted recalculation from the posted counts gives a risk difference of 0.123, with a 95% confidence interval from -0.001 to 0.248 and p = 0.053. The registry flags this discrepancy, so the sponsor’s own analysis takes precedence. Details of the original sample-size justification, missing-data methods, interim analyses and full statistical plan are not reported in the registry record.