ESSENCE Study: Efficacy and Safety of SD-101 Cream in Participants With Epidermolysis Bullosa: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for ESSENCE Study: Efficacy and Safety of SD-101 Cream in Participants With Epidermolysis Bullosa (NCT02384460), a randomized phase 3 study. The primary outcome is Time To Complete Target Wound Closure Within 3 Months.

2. Clinical Question

The trial's broader aim was to assess efficacy and safety of SD-101-6.0 cream compared with placebo in treating skin lesions in participants with epidermolysis bullosa. The registry lists secondary outcomes covering target-wound closure at Month 1 and Month 2, body surface area index (BSAI) measures at Month 3, and itching and pain scores at Day 7. Those outcomes address additional aspects of wound burden and symptoms, but they do not change the definition of the primary question.

3. Trial Design

The registry describes ESSENCE as a Phase 3, randomized, parallel-group, multi-center, double-blind, placebo-controlled study with quadruple masking. Participants were assigned to SD-101-6.0 cream or placebo (SD-101-0.0) cream. Both were applied topically once a day to the entire body for 90 days. The registry lists enrollment as 169 and the study status as completed. The study began on 2015-03-11, and the primary completion date is 2017-07-05.

Randomization is intended to make treatment groups comparable on average, while masking can reduce the influence of treatment knowledge on care, assessment, and reporting. These are general design principles; the registry record does not describe the randomization sequence, allocation concealment, or which roles were included in quadruple masking. It also does not report the original allocation ratio or give a detailed account of how participants were recruited across study centers.

The primary endpoint focused on time to target-wound closure within 3 months. The registry says that wounds were monitored at each study visit, and that participants without a response within 3 months, or who withdrew before closure confirmation, were censored. Its stated analysis population was the ITT population with post-baseline wound-closure data whose target wound closed within 3 months. The record does not explain in detail how that endpoint-specific population relates to all randomized participants or how missing observations were handled for each outcome.

The registry lists five secondary outcomes and reports analyses for selected outcomes, including BSAI and itching. It also reports adverse-event counts. The original sample-size justification, the trial's prespecified statistical analysis plan, and whether interim analyses were planned are not reported in the registry record. Planning illustrations based on the observed effects are separate from the trial's original design assumptions.

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: Participants had to be \>1 month of age with a diagnosis of simplex, recessive dystrophic, or junctional non-Herlitz Epidermolysis Bullosa (EB) and a target wound with a surface area of 10 to 50 cm\^2 and ≥21 days old to be considered for participation. Participants who did not meet all inclusion/exclusion criteria were eligible for rescreening.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT population with post-baseline wound closure data and whose target wound had closed within 3 months.

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: The Intent-to-treat (ITT) population included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Time To Complete Target Wound Closure Within 3 Months, measured over From baseline to Month 3 visit.

The primary endpoint was mean time to complete target-wound closure within 3 months. Time began on the date of the first administration of study drug and ended on the date of target-wound closure. Closure required skin re-epithelialization without drainage. The endpoint therefore captures how long closure took for target wounds that closed within the specified period, rather than simply whether a wound was closed at one visit.

The registry says wounds were assessed at each study visit. Participants who did not have a response within 3 months, or who withdrew before closure was confirmed, were censored. In general, censoring is a way to account for follow-up ending before the event is observed; it does not mean that the event occurred at the censoring time. The registry says the primary endpoint displays mean time to closure using a Kaplan-Meier approach, and separately reports a Cox model analysis.

This endpoint can be useful when the timing of an event matters and participants may have different follow-up, but interpretation depends on who is included and how censoring is handled. Here, the registry describes the analysis population as ITT participants with post-baseline wound-closure data whose target wound closed within 3 months. The broader handling of participants whose wounds did not close, or who withdrew earlier, is not fully detailed in the registry record. The reported endpoint should therefore be read as a time-to-closure result within the stated analysis framework, not as a complete description of all wound outcomes for every participant.

7. Results Posted in the Registry

• SD-101-6.0 Cream: mean 41.60 versus 53.60 on control; difference -12.00 (95% CI -23.57 to -0.43), standardized effect d = -0.44; z-test p = 0.042.

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.

Change From Baseline In Body Surface Area Index (BSAI) Of Lesional Skin At Month 3 Visit

• 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:
  • SD-101-6.0 Cream: mean -4.64 versus -5.32 on control; difference 0.68 (95% CI -3.14 to 4.50), standardized effect d = 0.06; z-test p = 0.727.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SD-101-6.0 Cream and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline In BSAI Of Total Body Wound Burden At Month 3 Visit

• 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:
  • SD-101-6.0 Cream: mean -3.05 versus -2.92 on control; difference -0.13 (95% CI -2.39 to 2.13), standardized effect d = -0.02; z-test p = 0.912.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SD-101-6.0 Cream and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline In Itching Score At Day 7

• 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:
  • SD-101-6.0 Cream: mean -0.50 versus -0.30 on control; difference -0.20 (95% CI -0.60 to 0.20), standardized effect d = -0.16; z-test p = 0.328.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SD-101-6.0 Cream and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the assessment beyond the primary time-to-closure measure. They cover complete target-wound closure at Month 1 and Month 2, BSAI measures at Month 3, and itching and pain scores at Day 7. The reported numerical analyses include BSAI outcomes and itching, but detailed numerical estimates for every listed secondary outcome are not reported in the registry record.

Across the posted analyses, the sponsor's BSAI comparisons have confidence intervals that include no difference, and the reported itching odds-ratio interval includes 1. This does not establish that the groups are identical; it indicates that those analyses do not clearly separate the estimates from their respective null values. The available secondary results do not remove the need to interpret the primary endpoint on its own terms, particularly because the primary summary-statistic recalculation and sponsor's time-to-event analysis differ.

Secondary outcomes can help describe whether findings are consistent across related measures, time points, and outcome types. They are not automatically confirmatory evidence for the primary question. The registry record does not report a multiplicity adjustment or a hierarchy for testing the secondary outcomes. General statistical explanation: when many outcomes are examined, the chance of at least one apparently notable result can increase, even if none represents a real effect. Without a reported adjustment or prespecified testing sequence, unadjusted secondary results carry less weight than a clearly defined primary analysis and should be treated as exploratory context.

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

• Percentage Of Participants Experiencing Complete Closure Of Their Target Wound At Month 1 And Month 2 Visits
• Change From Baseline In Body Surface Area Index (BSAI) Of Lesional Skin At Month 3 Visit
• Change From Baseline In BSAI Of Total Body Wound Burden At Month 3 Visit
• Change From Baseline In Itching Score At Day 7
• Change From Baseline In Pain Score At Day 7

9. Statistical Interpretation

10. Statistical Methods Explained

The endpoint combines event timing with incomplete follow-up. The registry states that target wounds were monitored for closure at each visit, and that participants were censored if they had no response within 3 months or withdrew before closure confirmation. General statistical explanation: in time-to-event analysis, censoring records that the event was not observed during the available follow-up; it allows the analysis to use the time under observation without treating the censoring point as an event. The assumptions and exact implementation of censoring matter, but the registry record does not describe them in detail.

Why use a time-to-event method?

General statistical explanation: a Kaplan-Meier approach estimates how event-free experience changes over follow-up while incorporating censored observations. A Cox model compares event rates over time through a hazard ratio. These methods address timing and censoring, unlike a basic comparison of group means that uses only the posted summary values. The registry says the primary endpoint displays mean time to closure using a Kaplan-Meier approach and reports a Cox Model Analysis, but it does not give the full model specification or explain the relationship between the displayed mean and the Cox estimate.

The sponsor's reported Cox estimate is a hazard ratio of 1.004, with a 95% confidence interval from 0.651 to 1.549 and p=0.985. General statistical explanation: a hazard ratio compares the event rate over time between groups under the model; a value near 1 is near equality in that relative measure. The confidence interval is broad enough to include values on either side of 1, so the estimate is not precise enough to distinguish a range of possible relative event rates. The ratio should not be read as a difference in mean days.

What does the recalculation represent?

The unadjusted recalculation uses the posted arm means and dispersions to estimate a mean difference. For the primary summaries, the group means are 41.6 and 53.6 days, and the recalculated difference is -12.0 days. General statistical explanation: a mean difference gives the average separation between two group means on the measurement scale. The associated recalculated confidence interval and p-value rely on a simple comparison of the posted summary statistics. They do not recreate the sponsor's time-to-event analysis, and they do not account for information that is not present in the group summaries.

The arm summaries report standard deviations. A standard deviation describes variation among observed measurements within a group; it is not the uncertainty of the estimated mean. The comparison also reports standard errors for the group means. General statistical explanation: a standard error describes the sampling uncertainty of an estimate, while a standard deviation describes spread among observations. Confusing the two can lead to incorrect conclusions about precision.

How should confidence intervals and p-values be read?

General statistical explanation: a confidence interval gives a range of estimates compatible with the data and the method used, at the stated confidence level. A p-value describes how unusual the observed result, or a more extreme one, would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The sponsor's primary p-value and the unadjusted recalculated p-value come from different analyses, so they should not be treated as interchangeable evidence.

The registry reports a 95% confidence interval for the sponsor's Cox analysis. The recalculated contrast has a separate confidence interval based on the summary-statistic comparison. For the BSAI outcomes, the sponsor reports mixed-model analyses and least-squares mean differences; those adjusted model estimates need not match an unadjusted difference reconstructed from arm summaries. The itching outcome is reported using a logistic regression and an odds ratio. General statistical explanation: these estimates answer different statistical questions and use different scales; a difference in units, model, or adjustment set can yield results that do not numerically align.

Why can over-dispersion matter?

General statistical explanation: over-dispersion occurs when observed variation is greater than a model's assumptions allow. If a model understates variation, its standard errors may be too small and its confidence intervals too narrow. The registry does not report whether over-dispersion was assessed or how it would apply to these analyses, so it should not be assumed to have been present or corrected. More generally, the model and uncertainty calculation should match the outcome type and data structure.

The planning illustrations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They consider effects set at stated fractions of the observed effect. General statistical explanation: under these assumptions, smaller effects require larger samples to have a similar chance of detection. The resulting figures are planning illustrations derived from observed estimates, not a record of the trial's original design process. The original sample-size justification, planned analysis details, and interim-analysis procedures are not reported in the registry record.

11. Confidence Intervals and Precision

Precision concerns how tightly an estimate is determined by the data and analysis. The sponsor's primary Cox estimate is 1.004, with a 95% confidence interval from 0.651 to 1.549. That interval includes 1, the value corresponding to no relative difference in the hazard ratio scale, and covers estimates on either side. The point estimate alone therefore gives an incomplete account of uncertainty.

The unadjusted recalculation gives a mean difference of -12.0 days and an interval that lies below zero. This interval comes from a different analysis of the posted means and dispersions. It should not be interpreted as a more precise version of the sponsor's Cox result: one estimates a mean difference in days, while the other is a time-to-event hazard ratio. The registry flags a discrepancy, so the sponsor's analysis takes precedence.

For the secondary BSAI analyses, the sponsor reports 95% confidence intervals that include zero for the least-squares mean differences. For itching, the reported odds-ratio interval includes 1. In general, an interval that includes the null value means the data and method do not clearly separate the estimate from no difference at the stated confidence level. It does not prove that the groups are identical.

Confidence intervals also do not capture every source of uncertainty. They reflect the statistical method and assumptions used, while uncertainties about the endpoint population, censoring, missing data, and multiplicity may require additional information. The registry record does not report a complete analysis plan or enough detail to evaluate all such choices. Precision should therefore be considered alongside the analysis definition and the discrepancy in the primary result, rather than inferred from a single interval or p-value.

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 for 80% power and participants per arm for 90% power. They are not total event counts: the posted comparisons are treated as continuous-outcome comparisons for these planning illustrations. In general, 80% power means an 80% chance of detecting the specified effect at the stated significance level if that effect and the planning assumptions are correct. The 90% column represents a higher target chance of detection under the same conditions. Neither value is a probability that the treatment effect is real.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses an effect set at a stated fraction of the observed effect. The values are derived from the observed comparison and are illustrations for planning, not the trial's original sample-size calculation. The trial's own design assumptions and sample-size justification are not reported in the registry record.

As the assumed effect becomes smaller, more participants are generally needed to distinguish it from random variation at a comparable power target. This is why scenarios based on a reduced fraction of the observed effect require larger per-arm sample sizes than scenarios based on the full observed effect. The displayed curve should be interpreted in that same planning context: it relates an assumed effect size to the sample size implied by the stated assumptions. These figures are not observed power; they do not measure the probability that this completed trial detected its true effect.

Planning estimates are sensitive to assumptions about variability, allocation, analysis, and the effect worth detecting. The illustrations use the observed effect as their starting point, which may itself be uncertain, particularly when the estimate is imprecise or when the reported analysis differs from a simple recalculation. They should not be read as evidence that the trial was or was not adequately designed.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -12.000; pooled standard deviation σ = 27.202.
2. n = 2 × (1.96 + 0.842)² × 27.202² / -12.000² = 80.7, rounded up to 81 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -12                      # observed difference in means
sigma <- 27.2017252860289                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2384460)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 81 (80% power), 108 (90% power)
 75% of observed effect: n per arm = 144 (80% power), 192 (90% power)
 50% of observed effect: n per arm = 323 (80% power), 432 (90% power)
power.t.test: 81.6 
Simulated power at n = 81 per arm: 0.796 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry's own primary analysis is a Cox model with a hazard ratio of 1.004, a 95% confidence interval from 0.651 to 1.549, and p=0.985. A separate unadjusted recalculation from the posted group means estimates a mean difference of -12.0 days, with an unadjusted p-value of 0.042 and a confidence interval lying below zero. The difference between these results is flagged in the registry analysis.

These estimates are not directly interchangeable. The recalculation uses group-level means and dispersions to compare average time in days. The Cox analysis uses a hazard ratio for a time-to-event outcome and can incorporate event timing and censoring. The registry does not provide enough detail about the model, endpoint population, or censoring implementation to identify why the results differ.

Because the record flags a discrepancy, the sponsor's own analysis takes precedence. The recalculation is best treated as an unadjusted check on the posted summary values, not as a correction to the sponsor's model or a substitute for a prespecified analysis. The record does not report the full statistical analysis plan needed to assess whether the Cox analysis was the planned primary method or to reconcile every analytic choice.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists several secondary outcomes in addition to the primary time-to-closure endpoint. It does not report whether the analyses were arranged in a prespecified hierarchy, whether family-wise error or another multiplicity procedure was used, or whether secondary p-values were adjusted. This information is important because examining multiple outcomes can increase the chance of a false-positive result across the set.

General statistical explanation: multiplicity refers to the problem of drawing conclusions from several statistical tests at once. A correction or testing hierarchy can control the risk of false-positive findings, but it may also change how much evidence each result provides. If no adjustment is reported, individual secondary p-values should not be treated as if they came from a single isolated test. The record's lack of a reported procedure does not prove that no procedure was used; it means the approach is not reported in the registry record.

The record also gives limited detail about missing data. For the primary endpoint, it says participants were censored if they did not have a response within 3 months or withdrew before closure confirmation, and it defines an analysis population with post-baseline wound-closure data whose target wound closed within 3 months. It does not fully explain how other missing observations were handled, how many participants were excluded from each outcome analysis, or whether sensitivity analyses assessed alternative missing-data assumptions.

The distinction between censoring and missing data is relevant. General statistical explanation: censoring is a time-to-event analysis status indicating that the event was not observed during a participant's available follow-up; missing data can arise when a measurement or outcome is unavailable. These situations can overlap but are not identical. The registry's description does not give enough detail to evaluate the assumptions behind censoring or to assess how incomplete measurements may affect each analysis.

The registry identifies an ITT population for the primary endpoint, but the endpoint-specific description also restricts that population to participants with post-baseline wound-closure data whose target wound closed within 3 months. The record does not clarify how that restriction was implemented relative to the randomized population. The analysis populations for every secondary outcome and the full prespecified statistical plan are not reported in the registry record.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pyrexia (2.4%), influenza (2.3%), wound (1.2%), aggression (1.2%), anemia (1.1%).

The registry reports serious adverse events for 82 participants at risk in the SD-101-6.0 cream group, with 4 affected, and for 87 participants at risk in the placebo group, with 8 affected. It reports other adverse events for 82 at risk in the SD-101-6.0 cream group, with 49 affected, and for 87 at risk in the placebo group, with 46 affected. Deaths are reported as 0 in the SD-101-6.0 cream group and 1 in the placebo group.

These counts describe the posted safety record; they do not by themselves establish that an event was caused by the assigned cream. The registry lists serious-event terms and percentages including Pyrexia, 2.4%; Influenza, 2.3%; Wound, 1.2%; Aggression, 1.2%; Anemia, 1.1%; and Cardiopulmonary failure, 1.1%. The record does not provide a detailed account of event timing, duration, severity beyond the serious classification, or causal attribution.

Safety counts should be read alongside the group-specific numbers at risk and the registry's event definitions. A numerical difference between groups is descriptive and does not alone show whether it reflects treatment, chance, underlying disease, or other factors. The available counts are not a substitute for a full clinical safety assessment.

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

The registry records a randomized comparison of SD-101-6.0 cream with placebo cream, with mean target-wound closure times reported for the primary endpoint. A simple unadjusted calculation from those summaries yields a negative mean difference, but the sponsor's reported Cox analysis is a different result on a different statistical scale. Because the registry flags a discrepancy, the sponsor's analysis takes precedence. The record does not provide enough detail to reconcile the two results fully.

The sponsor's primary hazard-ratio confidence interval includes 1, and the reported p-value is 0.985. This means the sponsor's analysis does not provide a clear statistical separation from the null value on the hazard-ratio scale. It does not establish that the groups are equivalent, nor does it show that every possible difference is excluded. The interval remains compatible with a range of relative event rates.

Secondary outcomes provide additional observations about wound burden and symptoms, but the registry does not report a multiplicity procedure or detailed numerical results for every listed outcome. They should be read as supporting context rather than independent confirmation of the primary result. The safety record reports serious and other adverse events and deaths by group, but the counts alone do not establish causation.

These results do not, by themselves, establish whether SD-101-6.0 cream should be used or whether it changes outcomes in other populations or settings. The registry entry is a record of a particular trial's design and posted analyses. Important details about the original sample-size rationale, full analysis plan, missing-data methods, and the endpoint population are not reported in the registry record. Those limits, together with the discrepancy between the primary analyses, constrain how confidently the posted statistics can be interpreted.

18. Why This Trial Matters Statistically

This trial illustrates why the statistical measure must match the endpoint and analysis. The primary outcome concerns time to an event, and the registry reports a Cox model hazard ratio. A recalculation based on posted means instead estimates a difference in days. Although both use the same general trial comparison, they do not answer precisely the same statistical question and need not produce matching conclusions.

The discrepancy is especially consequential because the unadjusted recalculation and sponsor analysis differ in their statistical interpretation. The sponsor's Cox analysis takes precedence, but its reported interval is broad. This makes the distinction between a point estimate and its uncertainty central: a single estimate cannot convey how much variation in plausible effects remains compatible with the analysis.

The registry also demonstrates the importance of population definitions and censoring in time-to-event studies. Its primary outcome description specifies an ITT-derived population and censoring conditions, but does not fully explain the implementation. Such details affect what the endpoint estimate represents and how it should be generalized to the randomized group.

Finally, multiple secondary outcomes, incomplete reporting of some outcome details, and the absence of a reported multiplicity strategy limit the strength of secondary conclusions. Planning illustrations based on observed effects can explain how assumptions influence future sample sizes, but they are not evidence about the trial's original planning or its observed power. Together, these features make the record a useful example of reading results alongside methods, uncertainty, and reporting completeness rather than focusing on one number.

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 primary endpoint has an important population qualification: the registry describes an ITT population with post-baseline wound-closure data whose target wound closed within 3 months. It also says that participants without a response within 3 months or who withdrew before closure confirmation were censored. The record does not explain fully how these criteria relate to the randomized population, or how the reported mean time should be interpreted for participants who did not have observed closure.

The registry reports both a Kaplan-Meier-based mean time summary and a Cox model result, while the unadjusted recalculation is based on the posted arm means and dispersions. These are distinct approaches, and the record flags a discrepancy between the recalculation and the sponsor analysis. The full model specification and sufficient detail to reconcile the results are not reported in the registry record.

The record does not report the original sample-size justification, full prespecified analysis plan, interim-analysis procedures, multiplicity adjustments, or comprehensive missing-data methods. It also does not provide a complete numerical account of every listed secondary outcome in the analysis material. These reporting gaps limit evaluation of whether the posted analyses align with prespecified plans and how robust the results are to alternative assumptions.

Safety findings are presented as counts, with limited contextual detail about event timing, duration, or causal attribution. The counts can describe what was recorded but cannot establish that an event was caused by an intervention. Finally, the trial is identified as multi-center and Phase 3, but the registry record does not provide enough information to assess the representativeness of participants or the applicability of these results outside the study setting.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: ESSENCE Study: Efficacy and Safety of SD-101 Cream in Participants With Epidermolysis Bullosa — NCT02384460.
• Registry record last updated 2020-04-09; status last verified 2020-04.
• Results first posted 2018-10-16.
• 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

ESSENCE was a completed Phase 3, randomized, parallel-group, double-blind, placebo-controlled study with quadruple masking in participants with epidermolysis bullosa. The registry lists enrollment of 169. SD-101-6.0 cream and placebo cream were applied topically once a day to the entire body for 90 days.

The primary outcome was mean time to complete target-wound closure within 3 months. The sponsor reported a Cox model hazard ratio of 1.004, with a 95% confidence interval from 0.651 to 1.549 and p=0.985. An unadjusted recalculation from posted summary statistics differs; the registry flags this discrepancy, and the sponsor's own analysis takes precedence.

The registry also lists secondary wound, BSAI, itching, and pain outcomes and reports safety counts. The original sample-size justification, detailed statistical plan, multiplicity strategy, and fuller missing-data methods are not reported in the registry record.