Treatment of Keloids With Fractional Erbium Laser-Assisted 5-Fluorouracil Versus Laser-Assisted Corticosteroid: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Treatment of Keloids With Fractional Erbium Laser-Assisted 5-Fluorouracil Versus Laser-Assisted Corticosteroid (NCT04786210), a randomized phase 4 study. The primary outcome is Change in Patient and Observer Scar Assessment Scale (POSAS) Score From Baseline to Final Visit.

2. Clinical Question

3. Trial Design

The registry describes a randomized, triple-blinded, parallel-design, Phase 4 study at a single center. Its official title identifies it as a prospective study of laser-assisted 5-fluorouracil versus laser-assisted corticosteroid treatment for keloids. The condition listed is keloid scar, and NYU Langone Health is the sponsor. The study is marked completed, with a start date of 2021-01-30 and primary completion on 2022-12-16.

The intervention descriptions specify fractional erbium:YAG-assisted drug delivery of 5-fluorouracil or triamcinolone acetonide. The registry summary describes a split-scar approach: Site A and Site B each represent one half of a keloid scar on a subject. It also states that treatment was planned as a series of 4 sessions at approximately 4 week ± 1 week intervals, with monitoring for safety and continued benefit after the intervention period. The reported primary outcome timeframe is baseline to Week 16.

The record lists target enrollment of 20. The posted primary outcome summaries each include 13 observations per treatment group, while the adverse-event record lists 19 at risk in each group. The registry does not explain how these counts relate to one another or why they differ. Randomization and triple masking are recorded, but the method of allocation, the roles masked, and how the split-scar design was incorporated into the analysis are not reported in the registry record. The posted results list no reported analyses.

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:

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 Change in Patient and Observer Scar Assessment Scale (POSAS) Score From Baseline to Final Visit, measured over Baseline, Week 16.

The primary endpoint is change in POSAS score from baseline to the final visit, identified as Week 16. POSAS combines an observer component and a patient component. The observer assesses vascularity, pigmentation, thickness, relief, pliability, and surface area. The patient answers questions about scar characteristics. The component scores are summed to make a total score.

The total ranges from 12 to 120, with 120 representing the worst scar and 12 the lowest score. This makes the direction interpretable: a negative change indicates a lower score at the final visit than at baseline, while a positive change would indicate a higher score. The measure is used to capture scar features from both the clinician’s and the patient’s perspectives, rather than relying on a single physical measurement. The registry reports the mean and standard deviation of change for each treatment group. It does not report separate observer and patient component results, so the posted total-score result cannot show which component contributed most to the overall change.

7. Results Posted in the Registry

• Site B of Keloid Scar - TAC: mean -20.60 versus -20.00 on control; difference -0.60 (95% CI -8.94 to 7.74), standardized effect d = -0.06; z-test p = 0.888.

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 in Scar Measurement From Baseline to Final 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 deviations.
• Result:
  • Site B of Keloid Scar - TAC: mean -310.70 versus -368.70 on control; difference 58.00 (95% CI -449.87 to 565.87), standardized effect d = 0.09; z-test p = 0.823.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Site B of Keloid Scar - TAC and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary outcome: change in scar measurement from baseline to the final visit, expressed in cm^3. The posted group summaries and unadjusted comparison show considerable uncertainty in the estimated contrast. Its confidence interval spans values in either direction, and its unadjusted p-value does not provide a precise estimate of the comparative effect. The overall pattern is therefore not a clear contrast between treatments that would settle the uncertainty in the primary POSAS result.

The secondary measure and POSAS address related but different aspects of scar change. POSAS combines patient and observer ratings of scar characteristics, whereas the secondary endpoint is a scar measurement. Agreement across different measures could support a coherent interpretation, but one uncertain secondary comparison cannot independently confirm the primary result. Nor does a difference in the numerical scale or variability make the endpoints directly interchangeable.

Secondary results generally carry less weight than a prespecified primary outcome because they may be among several outcomes examined and can be more vulnerable to chance findings. The registry lists three outcome measures and one secondary outcome, but provides no reported analyses or multiplicity adjustment. The status of the other listed measures is not sufficiently described to establish which were analyzed or how their results were handled. Unadjusted secondary results should therefore be considered exploratory rather than treated as confirmatory evidence. They can contribute context, but they do not replace a clearly specified primary analysis or resolve limitations in the primary outcome’s precision.

The registry’s record does not describe whether the secondary measurement was assessed by blinded evaluators, how it was collected, or how missing measurements were handled. These details would help judge comparability and potential sources of measurement variability, but they are not reported in the registry record. Interpretation should remain limited to the posted summaries and their uncertainty, rather than extending to a broader claim about the treatments.

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

• Change in Scar Measurement From Baseline to Final Visit

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean change represent?

A mean change is the average difference between baseline and the final assessment among the observations included in a treatment group. For POSAS, decreases correspond to lower scores, and the registry defines higher scores as worse scars. The group means of -20.0 and -20.6 therefore describe average score reductions in the posted outcome summaries. They do not describe every participant’s change: individual responses can vary around a mean, as reflected by the reported standard deviations.

What is the between-group estimate?

The mean difference compares the average change in the TAC group with the average change in the 5-FU group. The reported estimate is -0.6 points. Its sign follows that comparison order: a negative estimate means the TAC group’s mean change is lower than the 5-FU group’s mean change. The value is near zero, but the estimate alone does not communicate how precisely the difference is known. That requires the confidence interval.

What does the standard deviation tell the reader?

The standard deviation describes spread among observed changes within a group. It is not the range of possible values, and it is not a confidence interval for the mean. Larger spread means that observed changes are more dispersed around the group mean. The reported standard deviations, 8.0 and 13.1, indicate that the observed changes varied within both treatment groups, with greater spread in the TAC group. Differences in spread can also affect how precisely group means and their contrast are estimated.

How should the confidence interval be read?

A confidence interval gives a range of values compatible with the data under the assumptions of the calculation. In repeated use, the method is designed to produce intervals that cover the underlying quantity at the stated rate. It is not a probability statement that the particular interval contains the true value, and it does not identify which values within the interval are most likely. For this comparison, the interval from -8.944 to 7.744 includes zero and allows a range of possible comparative effects in either direction. Its breadth signals that the posted estimate is imprecise.

What does the p-value contribute?

The unadjusted p-value of 0.888 describes how compatible the observed comparison is with a null hypothesis of no mean difference, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. A large p-value does not demonstrate equality. In this result, the p-value is consistent with the confidence interval’s indication that the observed data do not sharply distinguish between zero and a range of positive or negative differences.

Why does the split-scar design matter?

When treatment sites occur on the same subject, outcomes from those sites may be related. A paired comparison can use within-subject information and account for that relationship. The registry records a parallel model while also describing Site A and Site B as halves of a scar on a single subject. It does not report whether or how the association between sites was included in the statistical analysis. The recalculated comparison is unadjusted and based on posted summary statistics; it cannot recover a paired analysis without information about the within-subject relationship. The registry’s original statistical plan is not reported.

Why can over-dispersion matter in other outcome settings?

General statistical context: over-dispersion occurs when observed variability is greater than a model expects. A model that understates variability can make standard errors too small and confidence intervals too narrow. The primary POSAS endpoint is continuous and reported with a mean and standard deviation, rather than as a count outcome with a count-model dispersion parameter. The registry does not report an over-dispersion assessment or a model-based analysis. The general concept is relevant when choosing models for outcomes, but it should not be taken to imply that over-dispersion was present in this trial.

The posted recalculations are unadjusted comparisons from summary statistics. The registry lists no reported analyses. No details of adjustment for baseline values, clustering, repeated measurements, or the split-scar pairing are reported in the registry record. These distinctions matter because the numerical estimate can be calculated from summaries while the inferential approach and its assumptions remain incompletely documented.

11. Confidence Intervals and Precision

Precision is principally reflected by the confidence interval around the between-group estimate. For the primary POSAS comparison, the mean difference is -0.6 points, with a 95% confidence interval from -8.944 to 7.744. This interval includes zero and spans values in both directions. It is therefore compatible with a range of comparative effects, rather than tightly pinning down a single value. Its width is important: the point estimate is close to zero, but the data do not precisely determine the size or direction of the underlying difference.

The standard deviations of 8.0 and 13.1 describe variation among observed changes in the two groups. They are not themselves measures of the uncertainty around the treatment contrast. The outcome summaries include 13 observations in each group. With limited outcome information and variation in change scores, a mean difference can remain imprecise even when the observed group means are similar.

The interval is an unadjusted recalculation from posted summary statistics. The registry describes a split-scar design, but does not report the within-subject correlation or a paired analysis. If the two sites on each subject are related, that information could affect the precision of a treatment comparison. The posted summaries do not allow that relationship to be reconstructed. The registry does not report a prespecified threshold for a clinically important difference, so the interval cannot be classified against such a threshold. It also does not report a formal equivalence margin. Thus, a confidence interval that includes zero does not, on its own, establish that the treatments have the same effect or that any difference is negligible.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not a record of the original trial’s design calculation. They give participants per arm for 80% power and participants per arm for 90% power. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The registry’s original sample-size assumptions are not reported in the registry record.

For planning at 100% of the observed primary effect, the illustration gives 5,137 participants per arm for 80% power and 6,877 participants per arm for 90% power. For planning at 75% of the observed effect, it gives 9,133 participants per arm for 80% power and 12,226 participants per arm for 90% power. For planning at 50% of the observed effect, it gives 20,548 participants per arm for 80% power and 27,508 participants per arm for 90% power.

The 80% column describes a design intended to have an 80% chance of detecting the specified effect under the calculation assumptions if that effect is true. The 90% column uses a higher target chance of detection. Detecting a smaller effect generally requires more participants, which is why the planning figures rise as the assumed effect fraction gets smaller. These figures are not observed power and should not be read as a retrospective measure of whether the completed study had adequate power. They are illustrations tied to an observed estimate that is itself uncertain; they do not establish what effect is clinically important or what sample size the investigators originally intended.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -0.600; pooled standard deviation σ = 10.854.
2. n = 2 × (1.96 + 0.842)² × 10.854² / -0.600² = 5,136.9, rounded up to 5,137 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.600000000000001                      # observed difference in means
sigma <- 10.8538011774677                     # 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(4786210)
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 = 5,137 (80% power), 6,877 (90% power)
 75% of observed effect: n per arm = 9,133 (80% power), 12,226 (90% power)
 50% of observed effect: n per arm = 20,548 (80% power), 27,508 (90% power)
power.t.test: 5137.8 
Simulated power at n = 5,137 per arm: 0.801 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary POSAS outcome and a secondary scar-measurement outcome, and it records three outcome measures in total. It lists zero reported analyses. No multiplicity strategy is reported in the registry record. When multiple outcomes or comparisons are examined, the chance of obtaining an apparently notable result by chance can increase. Statistical plans may address this through a hierarchy of outcomes or an adjustment to inference, but no such approach is described. The posted unadjusted secondary result should consequently be interpreted with caution, and the primary result should not be treated as a complete account of all planned analyses.

The registry does not report an analysis population, such as whether analyses were based on all randomized treatment assignments or only observations available at follow-up. It also does not report how missing outcome data were handled, whether participants withdrew, or whether any observations were excluded from the posted outcome summaries. The target enrollment is 20, while the primary outcome summaries report 13 observations per group and the safety record lists 19 at risk in each group. The registry does not explain the relationship among these counts. No reason for the differences can be inferred from the record.

The design description raises an additional analysis question. The registry identifies the study as parallel and randomized, while describing each treatment site as one half of a keloid scar on a subject. It does not report how allocation was performed within the split-scar setup, whether analyses accounted for correlation between sites on the same subject, or whether adjustment for baseline score was planned. Those details are important for interpreting standard errors and the intended treatment contrast.

Interim analyses, stopping rules, protocol deviations, and the full prespecified statistical plan are not reported in the registry record. Their absence does not establish that such procedures were or were not used. It limits the ability to check whether the reported outcomes, analysis choices, and timing followed the original plan. The inferential summaries should therefore be read as unadjusted comparisons from the posted data, not as a complete reconstruction of the trial’s planned analysis.

15. 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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists 19 participants at risk in each treatment group for the serious adverse event summary, with zero serious adverse events affecting participants in either group. It also lists zero deaths in each group. The other-adverse-event summary records 12 affected in each group. These are the registry’s group-specific figures; the record does not explain how the safety counts relate to the outcome-analysis counts.

A count of zero serious adverse events in the posted record does not demonstrate that a treatment has no serious risks. The study is small, and the record does not give event-specific follow-up detail or a description of how events were collected. The absence of listed serious-event terms is consistent with the reported zero serious events, but it should not be interpreted as proof that no event could occur. Likewise, the other-adverse-event counts do not establish that the types or severity of events were the same. Safety results describe what was recorded for the study groups and should be read within the limits of the registry’s reporting.

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

The posted results show similar average POSAS score changes in the two treatment groups, with a small estimated difference between their means. The confidence interval is wide and includes zero, so the comparison does not precisely establish the direction or size of a difference. The unadjusted p-value is also consistent with substantial uncertainty. These findings do not show that the treatments are equivalent, and they do not prove that either treatment is ineffective.

The group averages moved toward lower POSAS scores, but a before-and-after change within a treatment group is not the same as evidence that the treatment caused the change. The registry does not report a no-treatment comparison. The between-treatment contrast addresses relative change under the two listed interventions, not whether either intervention outperforms no treatment or another approach. The registry also does not report a threshold for a clinically important POSAS difference, so the result cannot be judged against such a threshold.

General statistical context: a nonsignificant result is not the same as evidence of no effect. To support a claim that differences are small enough to be unimportant, a study would typically need a prespecified margin and a sufficiently precise interval relative to that margin. Neither an equivalence margin nor a non-inferiority margin is reported in the registry record.

The design and reporting details also constrain interpretation. The study is described as split-scar, but the posted comparison does not report a paired analysis or within-subject correlation. The primary outcome summaries include 13 observations per group, while the safety record lists 19 at risk per group, and the registry does not explain the discrepancy. Missing-data procedures, analysis populations, and detailed statistical methods are not reported. The appropriate conclusion is therefore limited: the posted summaries do not precisely distinguish the average POSAS changes between the two treatment groups, and further claims about equivalence, causation, or broader applicability are not established by this record.

17. Why This Trial Matters Statistically

This trial is statistically notable because its clinical setup is described as split-scar, while its registry model is listed as parallel. When two treatments are applied to sites on the same subject, outcomes may be associated. A paired analysis can account for that association, but the registry does not report whether such an analysis was used. The posted summary-based comparison gives a transparent numerical contrast, yet it cannot recover the information in the relationship between sites. This distinction can affect uncertainty, not just presentation.

The primary endpoint uses a combined patient and observer score. That approach captures more than one perspective on scar characteristics, but the total score alone cannot show whether patient ratings and observer ratings changed in similar ways. Separate component results are not reported. The secondary scar-measurement endpoint adds a different kind of outcome, but its uncertainty and lack of reported multiplicity handling limit its role as corroborating evidence.

The record also illustrates why outcome counts and enrollment targets should not be treated as interchangeable. The target enrollment is 20, the primary outcome summaries include 13 observations per group, and the adverse-event summary lists 19 at risk per group. Without an explanation of these counts, readers cannot determine from the registry alone how outcome availability, follow-up, and safety monitoring align.

Finally, the estimated primary difference is close to zero, but the confidence interval remains broad. That combination is a useful reminder that a small point estimate is not the same as a precise finding. The trial’s statistical contribution is best understood through the estimate and its uncertainty together, alongside the limitations in the registry’s reporting of analysis methods and participant flow.

18. 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 comparison is based on 13 observations in each group, while the registry lists a target enrollment of 20. It does not explain why these counts differ or whether all enrolled participants contributed to the outcome summaries. The safety record lists 19 at risk in each group, but the relationship between those counts and the outcome-analysis groups is not reported in the registry record. This prevents a clear assessment of outcome availability and follow-up.

The split-scar description means sites within a subject may be related, but no within-subject correlation or paired analysis is reported. The registry also identifies a parallel model, leaving the analytical treatment of the split-scar structure unclear. The unadjusted recalculation from summary statistics cannot determine whether the investigators used a different approach, and the registry lists no reported analyses.

The record does not report the original sample-size justification, analysis population, missing-data strategy, allocation method, roles masked, or detailed statistical plan. It does not report a clinically important difference or an equivalence margin for POSAS. The primary result therefore cannot be judged against a stated clinical threshold, and a nonsignificant comparison cannot establish equivalence.

The available summary also does not separate POSAS patient and observer components, so it cannot identify which perspectives drove the total score. The registry lists one secondary outcome but no reported analyses or multiplicity approach. The study is identified as single-center, which limits how directly its findings can be generalized to other settings. These are limitations of what the registry record reports; they do not establish that unreported methods or assessments were not conducted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Treatment of Keloids With Fractional Erbium Laser-Assisted 5-Fluorouracil Versus Laser-Assisted Corticosteroid — NCT04786210.
• Registry record last updated 2024-03-26; status last verified 2024-02.
• Results first posted 2024-03-26.
• 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.

22. Record Summary

The registry describes a completed, randomized, triple-blinded, single-center Phase 4 study of fractional erbium:YAG-assisted 5-fluorouracil versus triamcinolone acetonide for keloid scars. It gives a target enrollment of 20 and a primary outcome of change in POSAS score from baseline to Week 16. The study summary describes a split-scar treatment approach.

The posted primary group means are -20.0 for 5-FU and -20.6 for TAC. The unadjusted mean difference is -0.6, with a 95% confidence interval from -8.944 to 7.744 and p = 0.888. The interval indicates substantial uncertainty and includes values in either direction. The registry lists zero serious adverse events and zero deaths in each group, alongside 12 affected by other adverse events in each group. The registry record does not report the original statistical plan, missing-data approach, or how the split-scar design was handled in analysis.