Controlled Study of the Occurrence of Actinic Keratosis on the Face After Cryotherapy + Aminolevulinic Acid (ALA) Photodynamic Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Controlled Study of the Occurrence of Actinic Keratosis on the Face After Cryotherapy + Aminolevulinic Acid (ALA) Photodynamic Therapy (NCT02239679), a randomized phase 2 study. The primary outcome is Total Number of AKs in Treatment Area.

2. Clinical Question

3. Trial Design

The registry describes a randomized, double-masked, parallel phase 2 study. Enrollment was 166, and the record gives the study status as completed. The recorded start was 2014-09 and primary completion was 2016-07. Actinic keratosis was the listed condition. The sponsor was DUSA Pharmaceuticals, Inc.

All three regimens included cryotherapy. ALA X2 consisted of cryotherapy followed by 2 aminolevulinic acid plus BLU-U treatments; ALA X3 consisted of cryotherapy followed by 3 such treatments. The vehicle group received cryotherapy followed by 2 or 3 topical vehicle plus BLU-U treatments, and the registry says these vehicle recipients were considered a single treatment group. It also describes the vehicle allocation as randomized 1:1 to be balanced for the two active groups. The record does not give further allocation details or explain how masking was maintained.

The primary endpoint was evaluated at Week 52. Its analysis population was defined as observed data from subjects still on-study at that time. This is important when interpreting the reported group sizes: the endpoint summary does not represent every enrolled participant. The registry record does not report the amount or pattern of missing Week 52 data, or the method used to handle missing observations.

The registry lists 69 outcome measures and 5 analyses, with secondary outcomes including the proportion of subjects with 0 AKs, satisfaction, recurrence rate, and duration of response. The quantitative secondary summaries available for interpretation include the Week 4 zero-AK count and duration of response within 52 weeks after baseline. Results for the other listed secondary outcomes are not reported in the registry record. The original protocol's sample-size rationale, detailed analysis plan, and further design specifications are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis population consisted of observed data; ie. subjects remaining on-study at Week 52.

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 Total Number of AKs in Treatment Area, measured over Week 52.

The primary endpoint is the total number of actinic keratoses in the treatment area at Week 52, reported as a least-squares mean in lesions with standard errors. It counts observed lesions that either recurred after on-study cryotherapy or newly occurred. Baseline lesions in the treatment area, up to a maximum of 2, were excluded from this endpoint.

A lesion count addresses the burden of visible lesions in the treated area at a specified follow-up time. Including recurrent and newly occurring lesions makes the endpoint relevant to the occurrence of AKs after the initial cryotherapy and subsequent assigned treatment. It is not simply a count of lesions cleared immediately after treatment; the endpoint reflects the count at Week 52 under the stated definition.

The analysis population is also part of the endpoint's meaning. The registry says the primary analysis used observed data from subjects remaining on-study at Week 52. Accordingly, the reported summaries describe that observed population, not necessarily all randomized participants. Without information about missing data or the reasons participants did not remain on-study, the degree to which those summaries represent the full randomized groups cannot be assessed.

Least-squares means ordinarily refer to model-based group means, but the registry does not provide the primary model details in the endpoint description. The posted group summaries give the means and standard errors; the sponsor-reported comparison is identified as ANCOVA. The registry record does not report a complete primary endpoint analysis specification or an adjusted effect estimate with its confidence interval.

7. Results Posted in the Registry

• ALA X3: mean 2.10 versus 3.00 on control; difference -0.90 (95% CI -3.33 to 1.53), standardized effect d = -0.14; z-test p = 0.467.
• VEH-PDT: mean 4.70 versus 3.00 on control; difference 1.70 (95% CI -0.75 to 4.15), standardized effect d = 0.27; z-test p = 0.175.

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 Subjects With 0 AKs

• 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:
  • ALA X3: 61.4% (35/57) versus 68.6% (35/51) on control; risk difference -7.2 percentage points (95% CI -25.2 to 10.7), risk ratio 0.89 (0.68–1.18); unadjusted two-proportion z-test p = 0.433.
  • VEH-PDT: 50.0% (27/54) versus 68.6% (35/51) on control; risk difference -18.6 percentage points (95% CI -37.1 to -0.2), risk ratio 0.73 (0.53–1.01); unadjusted two-proportion z-test p = 0.052.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ALA X3 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between VEH-PDT and the control. The interval gives the range of effects that remain compatible with the data.

Duration of Response

• 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:
  • ALA X3: mean 33.30 versus 35.90 on control; difference -2.60 (95% CI -10.25 to 5.05), standardized effect d = -0.13; z-test p = 0.506.
  • VEH-PDT: mean 25.90 versus 35.90 on control; difference -10.00 (95% CI -17.94 to -2.06), standardized effect d = -0.49; z-test p = 0.014.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ALA X3 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for VEH-PDT than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span different questions: whether participants had 0 AKs at a follow-up assessment, satisfaction, recurrence, and duration of response. The registry lists eight secondary outcomes, but quantitative results for all of them are not reported in the registry record. The available summaries include Week 4 counts of participants with 0 AKs and means for duration of response within 52 weeks after baseline. They do not provide a complete secondary-outcome picture.

These outcomes are related to the primary Week 52 lesion count, but they are not interchangeable. A zero-AK count at Week 4 captures a status at that time, while duration of response describes a period of response. The primary endpoint is a count at Week 52 that includes recurrent and newly occurring lesions and excludes baseline lesions under the endpoint definition. Patterns across distinct measures can differ without being contradictory.

The recalculated secondary comparisons are unadjusted and are not identified as sponsor-reported inferential analyses. They should therefore be treated as exploratory context, not as independent confirmation of the primary result. The registry record does not report whether the secondary outcomes were prespecified in a detailed analysis plan, how repeated assessments were handled, or whether multiplicity was controlled. When many outcomes and comparisons are examined, some apparently notable results can arise by chance. Without an adjustment plan, individual secondary p-values carry less weight than a prespecified, appropriately analysed primary result.

The secondary information should be read as incomplete: unavailable results for satisfaction, recurrence rate, and other listed outcomes are not evidence of no effect or of no events. They are simply not reported in the registry record. The primary interpretation should remain anchored to its stated endpoint and the sponsor-reported analysis, with secondary outcomes offering limited supporting context.

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

• Proportion of Subjects With 0 AKs
• Subject Satisfaction Score
• Proportion of Subjects With 0 AKs
• Proportion of Subjects With 0 AKs
• Proportion of Subjects With 0 AKs
• Proportion of Subjects With 0 AKs
• Recurrence Rate
• Duration of Response

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous count: the number of lesions in the treatment area at Week 52. Although lesion counts are discrete observations, the registry labels the reported summary as a least-squares mean and gives a standard error. A mean describes the average count in the analysis population; a standard error describes uncertainty in estimating that mean. The standard error is not the spread of individual participants' lesion counts.

The registry's sponsor-reported primary comparison is identified as ANCOVA. In general, analysis of covariance compares group outcomes while accounting for specified covariates. Adjustment can improve precision or address baseline differences when the model and covariates are appropriate. The registry record does not report which covariates were included, the adjusted estimate, or its confidence interval. The reported sponsor result is a superiority test comparing ALA X3 with VEH-PDT, with p = 0.017; the record does not state the test's estimate or confidence interval.

Separately, the posted summaries permit simple unadjusted recalculations of pairwise differences. These use the displayed group summary statistics and do not reproduce the sponsor's ANCOVA. For ALA X3 versus ALA X2, the recalculated mean difference is -0.9 lesions, with a confidence interval from -3.327 to 1.527 and unadjusted p = 0.467. For VEH-PDT versus ALA X2, the recalculated mean difference is 1.7 lesions, with a confidence interval from -0.754 to 4.154 and unadjusted p = 0.175. These calculations are labelled recalculated because they are derived from posted summary statistics rather than the reported adjusted model. The registry flags a discrepancy; the sponsor's own analysis takes precedence.

What does a confidence interval convey?

In general, a confidence interval describes the uncertainty around an estimated effect under the assumptions of the analysis. A narrower interval indicates greater precision; a wider interval indicates less precision. An interval that includes zero for a difference is compatible with no difference under the interval's construction, as well as with effects on either side of zero. The confidence level for the posted recalculated intervals is not stated in the registry record, so it should not be inferred from the values alone.

Why can over-dispersion matter for lesion counts?

In general, count data can vary more between individuals than a simple count model assumes. This is called over-dispersion. If present and not accounted for, it can make standard errors too small and confidence intervals too narrow. A model suited to the outcome and its variability can address this concern. The registry record does not report the distribution of individual lesion counts or enough model details to determine whether over-dispersion was assessed or how it was handled. The least-squares means and standard errors alone cannot answer that question.

How should the binary secondary outcome be read?

The Week 4 secondary outcome counts participants with 0 AKs. The displayed values are participant counts, not mean lesion counts. In general, a risk difference contrasts the proportions in the compared groups; it is a different effect measure from a mean difference. The recalculated risk differences and p-values are unadjusted. For ALA X3 versus ALA X2, the risk difference is -0.072, with a confidence interval from -0.252 to 0.107 and unadjusted p = 0.433. For VEH-PDT versus ALA X2, it is -0.186, with a confidence interval from -0.371 to -0.002 and unadjusted p = 0.052. These are not reported sponsor analyses.

The registry also provides a mean and standard deviation for duration of response. In general, the standard deviation describes variation among observations, whereas a standard error describes uncertainty in a mean. The duration comparison is a separate outcome with a different time interpretation from the Week 52 lesion count. Its recalculated differences are unadjusted and should not be treated as evidence that the primary endpoint had the same pattern.

What does the planning illustration represent?

The planning figures are calculated illustrations based on observed effects, under assumptions stated in the registry record. They are not the original study's design calculations and are not observed power. The original design assumptions are not reported in the registry record. These values describe hypothetical future sample sizes under the stated assumptions; they do not alter the interpretation of the observed trial results.

Across the analyses, it is important to distinguish the sponsor-reported test from the recalculated comparisons, the primary endpoint from secondary outcomes, and observed group summaries from model-adjusted estimates. The registry record does not report a comprehensive statistical analysis plan, including details of model diagnostics, missing-data procedures, or multiplicity control. Those omissions constrain how fully the analyses can be evaluated.

11. Confidence Intervals and Precision

The primary group summaries include standard errors of 0.91 for ALA X2, 0.84 for ALA X3, and 0.86 for VEH-PDT. These indicate uncertainty around the reported least-squares means, not the range of individual lesion counts. The group means are 3.0, 2.1, and 4.7 lesions, respectively. The registry record does not provide confidence intervals for these individual means.

The recalculated ALA X3 versus ALA X2 mean difference is -0.9 lesions, with a confidence interval from -3.327 to 1.527. The recalculated VEH-PDT versus ALA X2 difference is 1.7 lesions, with a confidence interval from -0.754 to 4.154. Both intervals include zero. Their breadth shows that the unadjusted summary comparisons are not highly precise about the size or direction of a difference. These intervals belong to the recalculations and should not be confused with an adjusted interval from the sponsor's ANCOVA, which is not reported.

A confidence interval is useful because it displays a range of effect estimates compatible with the data and analysis assumptions, rather than presenting a point estimate alone. It does not establish the probability that a particular effect is true. The confidence level for the displayed recalculated intervals is not reported in the registry record. The sponsor's p-value is reported without a corresponding effect estimate or confidence interval, limiting assessment of the adjusted result's precision.

For the secondary outcomes, the recalculated Week 4 risk-difference interval for ALA X3 versus ALA X2 runs from -0.252 to 0.107, while the interval for VEH-PDT versus ALA X2 runs from -0.371 to -0.002. For duration of response, the corresponding mean-difference intervals are -10.25 to 5.055 and -17.94 to -2.061. These intervals likewise describe unadjusted recalculations, not sponsor-adjusted results. Their interpretation should account for the exploratory nature of secondary comparisons and the lack of reported multiplicity adjustment.

Precision is also affected by the analysis population. The primary endpoint includes observed data from subjects still on-study at Week 52. Without a reported account of missing observations, it is not possible to judge whether missingness changed the composition of the analysed groups or altered the uncertainty represented by the summaries.

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 effects, not a record of the trial's original design assumptions. For these non-time-to-event comparisons, the values are participants per arm, not total events. The registry states the planning assumptions: two-sided significance level 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. Time-to-event planning tables, if present, use total events, but the comparisons discussed for this trial are not identified as time-to-event planning tables.

The 80% power column gives the illustrative participants per arm under which a future study would have an 80% chance of detecting the specified effect if the assumptions and effect were correct. The 90% power column gives the corresponding illustration for a 90% chance. Power is a property of a planned study under assumed conditions; it is not the probability that the observed trial result is correct. These figures are not observed power.

Rows describing 100%, 75%, and 50% of the observed effect show how the planning result changes when the target effect is set to a fraction of the effect seen in this trial. A smaller target effect is harder to distinguish from random variation, so it requires more participants per arm under the stated assumptions. For instance, the ALA X3 versus ALA X2 planning illustration lists 784 participants per arm for 80% power when planning for 100% of the observed effect and 3,133 when planning for 50% of that effect. Those are hypothetical planning quantities, not participants actually enrolled in this trial.

The planning calculations use the recalculated observed effects, so they inherit the limitations of those estimates. A small or uncertain observed effect can make such illustrations unstable, and the values should not be treated as a recommendation for a future trial without a new design assessment. The original trial's sample-size justification, anticipated effect, and planned power are not reported in the registry record.

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 = -0.900; pooled standard deviation σ = 6.356.
2. n = 2 × (1.96 + 0.842)² × 6.356² / -0.900² = 783.0, rounded up to 784 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 <- -0.9                      # observed difference in means
sigma <- 6.35647232233535                     # 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(2239679)
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 = 784 (80% power), 1,049 (90% power)
 75% of observed effect: n per arm = 1,393 (80% power), 1,864 (90% power)
 50% of observed effect: n per arm = 3,133 (80% power), 4,194 (90% power)
power.t.test: 784 
Simulated power at n = 784 per arm: 0.802 (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 reports an ANCOVA superiority analysis comparing ALA X3 with VEH-PDT, with p = 0.017. It does not provide the adjusted effect estimate, its confidence interval, or the covariates included in that model. The group summaries report Week 52 least-squares means of 2.1 lesions for ALA X3 and 4.7 for VEH-PDT, but those values alone do not reconstruct the adjusted comparison.

The simple recalculations use posted summary statistics and compare ALA X3 and VEH-PDT separately with ALA X2. They are unadjusted comparisons, not reproductions of the sponsor's ANCOVA. The registry explicitly marks a discrepancy between the sponsor's analysis and the recalculation. In that situation, the sponsor's own analysis takes precedence for the trial's reported inferential result. The recalculated values remain useful as transparent checks on the posted summaries, but they cannot replace the sponsor's model-based analysis.

The sponsor test's p-value conveys evidence against its tested null under the analysis model; it does not give the magnitude or precision of the adjusted effect. Without an estimate and confidence interval, readers cannot determine the range of adjusted effects compatible with the sponsor analysis or assess its clinical importance from that result alone. The registry record also does not report enough model detail to evaluate the ANCOVA specification.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists many outcome measures and multiple analyses, including a primary endpoint and several secondary outcomes. It does not report a multiplicity strategy, such as a testing hierarchy or an adjustment method, in the information available for this analysis. When several outcomes or pairwise comparisons are assessed, the chance of obtaining at least one small p-value by chance can increase. In general, multiplicity procedures control or account for that issue; without a reported plan, isolated secondary p-values should be interpreted cautiously.

The primary sponsor analysis is reported as an ANCOVA superiority test for ALA X3 versus VEH-PDT. The record does not report the full statistical analysis plan, the model covariates, an adjusted estimate, or a confidence interval for that comparison. Details such as the significance threshold for the sponsor's primary test and the handling of any planned comparisons are not reported in the registry record. The planning illustration's two-sided significance level 0.05 is a planning assumption, not evidence that the trial's original primary analysis used that threshold.

The endpoint population consists of observed data from participants remaining on-study at Week 52. The registry does not report how many randomized participants lacked Week 52 observations, why they were missing, or whether the missingness differed across groups. It also does not describe an imputation method, sensitivity analysis, or other missing-data procedure. In general, an observed-case analysis may be affected if the availability of outcome data is related to participant characteristics or outcomes. The record does not provide enough information to determine whether that concern arose in this trial.

The registry provides group-level summaries but not participant-level distributions. It does not report diagnostic checks, treatment of influential observations, or details sufficient to evaluate assumptions for the primary model. The stated use of ANCOVA identifies a method family but does not establish which adjustments were made or whether its assumptions were checked.

These omissions do not invalidate the posted findings, but they limit independent assessment of robustness and precision. They also reinforce the distinction between the sponsor-reported result and simple unadjusted recalculations. The sponsor result is the trial's reported analysis; the recalculations should not be presented as a replacement, and absent analyses should not be inferred.

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: acute myocardial infarction (1.9%), atrial fibrillation (1.9%), coronary artery disease (1.9%), upper gastrointestinal haemorrhage (1.9%), duodenal neoplasm (1.9%).

The registry reports serious adverse event counts by safety group: ALA X2 had 0 among 53 at risk, ALA X3 had 3 among 59 at risk, and VEH-PDT had 4 among 54 at risk. Other adverse events were reported for 13 among 53 at risk in ALA X2, 9 among 59 at risk in ALA X3, and 15 among 54 at risk in VEH-PDT. Deaths were recorded as 0 in each group.

These are event or participant counts as presented in the registry record; they do not, on their own, establish that treatment caused an event or that one regimen has a different safety profile. The record lists serious-event terms including acute myocardial infarction, atrial fibrillation, coronary artery disease, upper gastrointestinal haemorrhage, duodenal neoplasm, and angina unstable. The associated percentages listed for those terms are 1.9% for the first five and 1.7% for angina unstable. The registry record does not provide enough detail to infer causality, timing, or the relationship between every term and the group totals.

Safety counts should be read alongside the trial's duration, population, and reporting definitions. The registry does not report further detail on event severity beyond the serious and other categories in these summaries, nor does it provide a basis for broader safety conclusions.

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

The results describe a randomized, double-masked, parallel phase 2 study of regimens given after cryotherapy for facial actinic keratoses. The primary outcome was a Week 52 count of lesions in the treatment area among subjects with observed data who remained on-study. The posted group means and standard errors characterize that analysis population; they do not by themselves show how outcomes would have appeared for everyone enrolled.

The sponsor-reported ANCOVA comparison of ALA X3 with VEH-PDT has p = 0.017. Because the adjusted estimate and confidence interval are not reported, the magnitude and precision of that adjusted comparison cannot be fully assessed from the registry record. The simple unadjusted recalculations use a different comparison structure and do not reproduce the sponsor model. The registry flags a discrepancy, so the sponsor's own analysis takes precedence.

A p-value is not a measure of effect size, and it does not establish whether a difference is important to patients or clinicians. A confidence interval can communicate uncertainty around an estimate, but the sponsor analysis's interval is not reported. The recalculated intervals describe unadjusted comparisons only. No medical advice or treatment recommendation follows from these statistical summaries.

The secondary summaries address different aspects of outcome and are incomplete. Their unadjusted comparisons carry less weight where the registry does not report multiplicity control or a full analysis plan. Safety counts and the absence of recorded deaths in these groups are also descriptive; they do not establish that a regimen is safe or that adverse events were caused by treatment.

More complete interpretation would require details not reported in the registry record, including the sponsor model's effect estimate and covariates, missing-data information, a multiplicity plan, and results for the other listed outcomes. The record supports describing what was measured and what was reported, but not extending those findings beyond this study's population, endpoint, and analysis.

18. Why This Trial Matters Statistically

This trial illustrates why the analysis attached to a clinical outcome matters as much as the observed group summaries. The Week 52 endpoint is a lesion count, reported as least-squares means and standard errors, while the registry's sponsor-reported comparison uses ANCOVA. Those summaries and that adjusted comparison answer related but not identical statistical questions. Without the adjusted estimate and model details, the sponsor test cannot be translated into a complete account of effect size and precision.

It also demonstrates the value and limits of recalculation. A transparent unadjusted comparison can help readers understand the posted group summaries, but it cannot substitute for an adjusted analysis when the registry reports a discrepancy. The sponsor analysis takes precedence for the trial's reported inference; the recalculated comparisons should remain clearly labelled and interpreted as checks rather than definitive results.

The endpoint population raises another important issue. The primary analysis uses observed Week 52 data among participants remaining on-study. Without missing-data counts and methods, readers cannot tell how that restriction affects generalizability or uncertainty. This is a reminder that an endpoint's definition includes not only what is measured, but also whose data contribute to the analysis.

Finally, the trial includes multiple secondary outcomes, while the record does not report a multiplicity strategy or results for every listed outcome. Statistical interpretation therefore requires separating the primary analysis from exploratory secondary evidence and resisting conclusions from isolated unadjusted tests. This is broadly useful for clinical research: effect estimates, uncertainty, analysis populations, and reporting completeness all shape what a result can reasonably support.

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.

Several limitations are specific to the registry information for this trial. The primary endpoint population includes only observed data from subjects remaining on-study at Week 52. The registry record does not report the amount, reasons, or group distribution of missing Week 52 data, nor does it describe a missing-data method. This makes it difficult to assess whether the observed-case summaries reflect the randomized groups.

The registry reports the sponsor's ANCOVA p-value for ALA X3 versus VEH-PDT but not its adjusted effect estimate, confidence interval, or model covariates. The simple recalculations instead compare each relevant group with ALA X2 using posted summary statistics. Because the record marks a discrepancy, those recalculations cannot be treated as the trial's definitive inferential results.

The detailed protocol and statistical analysis plan are not reported in the registry record. In particular, the original sample-size rationale, planned power, multiplicity strategy, and full model specification are unavailable. The planning illustrations rely on observed effects and cannot establish what the original trial was designed to detect.

The registry lists eight secondary outcomes, but does not report quantitative results for all of them in the information available for interpretation. The available secondary comparisons are unadjusted, and their relationship to any prespecified testing plan is not reported. The safety summaries are counts and listed event terms; the record does not provide enough context to determine causality or fully characterize event timing and severity.

Finally, the primary endpoint counts lesions at Week 52 under a specific definition and in a specified treatment area. It does not by itself describe other outcomes, longer-term results beyond the stated timeframe, or outcomes in populations not represented by this study. These limitations call for bounded interpretation rather than extrapolation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Controlled Study of the Occurrence of Actinic Keratosis on the Face After Cryotherapy + Aminolevulinic Acid (ALA) Photodynamic Therapy — NCT02239679.
• Registry record last updated 2018-08-24; status last verified 2017-09.
• Results first posted 2017-09-21.
• 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

NCT02239679 is a completed randomized, double-masked, parallel phase 2 study of cryotherapy followed by aminolevulinic acid plus blue light or vehicle plus blue light in high-risk individuals with facial actinic keratoses. Enrollment was 166. The primary endpoint was the Week 52 total AK count in the treatment area, using observed data from subjects remaining on-study.

The sponsor-reported ANCOVA comparison of ALA X3 with VEH-PDT has p = 0.017; its adjusted effect estimate and confidence interval are not reported in the registry record. Simple unadjusted recalculations are also available, but the registry flags a discrepancy, so the sponsor's own analysis takes precedence. Secondary and safety summaries provide additional descriptive context, with important analysis and reporting details not reported.