To Compare Safety and Efficacy of Perrigo's Drug Compared to an FDA Approved Drug in the Treatment of Actinic Keratosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for To Compare Safety and Efficacy of Perrigo's Drug Compared to an FDA Approved Drug in the Treatment of Actinic Keratosis (NCT02459795), a randomized phase 3 study. The primary outcome is Number of Participants With Complete Clearance (Absence) of Actinic Keratosis Lesions.

2. Clinical Question

The study’s stated purpose was to compare safety and efficacy of Perrigo’s drug with an FDA-approved drug for actinic keratosis. The posted primary measure focuses on complete clearance rather than partial improvement or change in lesion count. It reports counts of participants who met that endpoint, not a continuous measure of the amount of change.

The registry record also posts recalculated comparisons between the test product and reference product, and between placebo and reference product. These are unadjusted risk-difference calculations from the posted counts. The sponsor’s reported analysis concerns only the test and reference products and uses an equivalence-ratio parameter. The record does not give an equivalence margin, so the meaning of the sponsor’s equivalence estimate cannot be judged against a stated clinical or statistical boundary.

3. Trial Design

This was a randomized, double-masked, parallel-group phase 3 trial sponsored by Padagis LLC. The registry lists 469 participants as enrolled and identifies actinic keratosis as the condition under study. The three intervention groups were Ingenol Mebutate (Perrigo), Ingenol Mebutate (Reference), and placebo gel. The record labels these arms Test Product, Reference Product, and Placebo Product, respectively.

The study is marked completed. Its recorded start was 2015-05, and its primary completion was 2015-12. The posted primary outcome covers baseline to Day 57. The record does not describe the precise randomization procedure, the masking procedures, or whether masking was maintained throughout follow-up. It identifies the study as randomized and double-masked, but further operational detail is not reported in the registry record.

The primary outcome counts were 71 of 150 participants in the test-product group, 71 of 160 in the reference-product group, and 9 of 75 in the placebo group. These denominators are for the per protocol population used for the primary endpoint. They are not the same as the total enrollment or the safety denominators posted for adverse events. The registry record does not explain the participant flow between enrollment, the per protocol population, and the safety population.

The record lists one primary outcome measure and one sponsor-reported analysis. The original sample-size justification, allocation ratio, statistical analysis plan, eligibility criteria, and timing of any interim analyses are not reported in the registry record. Randomization and masking are relevant features of the trial design, but they do not by themselves resolve questions about the handling of missing observations, analysis populations, or the prespecified interpretation of the comparisons.

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

Analysis population for the primary outcome, as defined in the registry: Per protocol population

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 Number of Participants With Complete Clearance (Absence) of Actinic Keratosis Lesions, measured over Baseline to Day 57.

The primary endpoint counts participants with complete clearance, defined in the registry as absence of actinic keratosis lesions, over the period from baseline to Day 57. It is a binary outcome: each participant either met the complete-clearance definition or did not. The posted values are counts of participants meeting the definition, paired with the number in the per protocol population for each group.

Complete clearance is useful as an endpoint because it expresses the outcome as whether a participant reached a clearly stated status, rather than only describing average change in lesion burden. That can make the result relatively direct to interpret. However, a binary endpoint does not show how close participants who did not meet the definition came to clearance, how many lesions remained, or how lesion burden changed over time. Those details are not reported as part of this primary measure.

The endpoint is assessed at Day 57, so it describes the recorded status at that time point, not durability beyond that assessment. The registry record does not report additional follow-up for this endpoint, the exact assessment procedure, or a definition of how lesions were counted or confirmed. Interpretation should therefore remain tied to the stated complete-clearance outcome, timeframe, and per protocol population.

7. Results Posted in the Registry

• Test Product: 47.3% (71/150) versus 44.4% (71/160) on control; risk difference 3.0 percentage points (95% CI -8.1 to 14.1), risk ratio 1.07 (0.84–1.36); unadjusted two-proportion z-test p = 0.601.
• Placebo Product: 12.0% (9/75) versus 44.4% (71/160) on control; risk difference -32.4 percentage points (95% CI -43.0 to -21.7), risk ratio 0.27 (0.14–0.51); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

What is being compared? The primary outcome is binary: a participant either had complete clearance by Day 57 or did not. For a binary outcome, a risk is the proportion of participants in a group who meet the outcome. A risk difference subtracts one group’s risk from the other’s. Its sign depends on which group is subtracted from which, so the direction of the comparison must be read alongside the arm labels. In the posted recalculations, test product is compared with reference product, and placebo is compared with reference product.

The reported risk differences are unadjusted recalculations from the posted summary counts. They do not account for any covariates or design features beyond the two groups’ observed counts. The record does not report an adjusted analysis for the primary outcome. A risk difference is expressed on the absolute probability scale, while a risk ratio or odds ratio expresses a relative comparison. These measures can communicate different aspects of the same data and should not be read as though their numerical values were interchangeable.

What does the confidence interval mean? In general, a confidence interval describes the range of effect estimates that are reasonably compatible with the observed data under the method’s assumptions. A wider interval means less precision; an interval that includes zero for a risk difference includes no difference among the values compatible with the data at that confidence level. It does not prove that the true difference is zero. A confidence interval that lies entirely on one side of zero indicates that zero is not within that interval, but it still does not establish the size or practical importance of an effect on its own.

How should the p-values be read? In general, a p-value measures how unusual the observed data, or data more extreme, would be if the null hypothesis and the test’s assumptions held. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. The recalculated p-values are explicitly unadjusted. The registry record does not report a multiplicity procedure for the comparisons, so the p-values should not be interpreted as multiplicity-adjusted confirmatory tests.

What is the sponsor’s reported method? The sponsor analysis compares the test and reference products using Yates correction and reports an equivalence ratio of 1.00 with a 90% confidence interval from -7.00 to 12.92. Yates correction is a continuity correction used in some categorical-data tests; in general, it adjusts a discrete count-based calculation when an approximation based on a continuous distribution is used. The record does not provide enough detail to reconstruct the sponsor’s full calculation, and it does not report a p-value for this analysis.

Equivalence testing asks whether the difference between groups is contained within prespecified bounds judged acceptably small. A point estimate near the null value does not alone demonstrate equivalence. The confidence interval must be assessed against the equivalence margins, and those margins are not reported in the registry record. The sponsor’s parameter is called an equivalence ratio, but the units and interpretation of its confidence limits are not explained. The posted estimate therefore cannot be evaluated as a complete equivalence test from the registry entry alone.

Why might over-dispersion matter? General explanation: over-dispersion occurs when observed variability is greater than a statistical model expects. It can make standard errors too small and confidence intervals too narrow if the analysis assumes less variability than the data contain. Over-dispersion is most often a concern for count outcomes with variation beyond a simple model; the posted primary outcome is a participant-level binary endpoint. The registry record does not report an over-dispersion assessment or a model that would permit one to be evaluated.

What is not described? The registry record does not report the original statistical analysis plan, any covariate adjustment, the method used to handle missing primary outcomes, or the details of the randomization and masking procedures. It does not report multiplicity control or interim analyses. These omissions limit what can be inferred about whether the posted comparisons match the trial’s original confirmatory plan. General statistical considerations can explain how the posted measures work, but they cannot fill in undocumented protocol choices.

10. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval. A narrow interval indicates that the estimate is more tightly constrained by the observed data under the calculation’s assumptions; a wide interval leaves a broader range of effects compatible with the data. The test-versus-reference recalculated risk-difference interval includes both negative and positive values. Thus, it includes the possibility of a difference favoring either group as well as no difference. The p-value of 0.601 is consistent with the interval not distinguishing the estimate from zero in this unadjusted comparison.

For the placebo-versus-reference recalculation, the risk-difference interval is entirely below zero when the comparison is expressed as placebo minus reference. The unadjusted p-value is <0.001. This interval is more clearly separated from zero than the test-versus-reference interval, but precision and statistical separation do not establish clinical importance. The registry record does not state a threshold for a clinically important difference.

The sponsor’s 90% confidence interval is reported for the equivalence-ratio analysis, but without the equivalence margin its precision cannot be judged against the intended decision rule. A confidence interval is informative only in relation to the parameter and the question being asked. The registry record does not explain the units of the reported limits.

All intervals describe sampling uncertainty under their respective methods; they do not account automatically for unreported design or analysis choices. The per protocol population, unexplained differences between analysis and safety denominators, and unreported handling of missing data are relevant to interpretation. The confidence intervals do not capture every possible source of uncertainty or bias.

11. 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 events. They are illustrations based on the observed effect in each comparison, then on smaller fractions of that observed effect. For the test-versus-reference comparison, the displayed planning counts rise from 4,453 per arm at 100% of the observed effect to 7,906 at 75% and 17,765 at 50% for the 80% power column. For the 90% power column, the corresponding entries are 5,960, 10,583, and 23,781.

For the placebo-versus-reference comparison, the 80% power illustrations are 30, 57, and 138 participants per arm for 100%, 75%, and 50% of the observed effect. The 90% power illustrations are 39, 76, and 184 participants per arm for those same assumed effect fractions. These are planning scenarios, not the enrollment targets used to design this trial; the trial’s original sample-size assumptions are not reported in the registry record.

General explanation: power is the probability that a specified statistical test will detect an effect of a chosen size under the assumptions of the calculation. The 80% and 90% columns represent different target probabilities for detecting the assumed effect if it were present. The calculations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. Smaller effects need more participants to distinguish them from random variation. These figures are planning illustrations, not observed power.

12. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.444; treatment proportion p₁ = 0.473; average p̄ = 0.459.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7047 = 1.3811.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7044 = 0.5928.
4. n = (1.3811 + 0.5928)² / (0.0296)² = 4,452.2, rounded up to 4,453 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.44375                          # control proportion
p1 <- 0.473333333333333                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2459795)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 4,453 (80% power), 5,960 (90% power)
 75% of observed effect: n per arm = 7,906 (80% power), 10,583 (90% power)
 50% of observed effect: n per arm = 17,765 (80% power), 23,781 (90% power)
power.prop.test: 4452.2 
Simulated power at n = 4,453 per arm: 0.801 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The sponsor-reported analysis compares the test and reference products using Yates correction. It reports an equivalence ratio of 1.00 and a 90% confidence interval from -7.00 to 12.92; no p-value is posted for this analysis. The registry record does not report the equivalence margin or explain the scale and interpretation of the interval limits. Without the margin, the reported interval cannot establish whether the sponsor’s equivalence criterion was met.

The recalculation instead uses the posted counts to estimate an unadjusted risk difference for test product versus reference product. Its confidence interval includes zero, and its p-value is 0.601. These analyses address related but distinct statistical questions and report different measures. A risk-difference calculation from summary counts does not replace the sponsor’s analysis, and the sponsor’s equivalence-ratio result cannot be reconstructed from the posted counts alone.

No discrepancy between the sponsor’s reported analysis and the recalculation is identified in the registry record. The sponsor analysis remains the trial’s reported analysis, while the recalculation is an unadjusted comparison based on the posted summary statistics. The original protocol and analysis plan are not reported, so the relationship between the sponsor’s method and any prespecified decision rule cannot be fully assessed.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome measure and one sponsor-reported analysis. It also supports two recalculated comparisons: test product versus reference product and placebo versus reference product. The posted recalculated p-values are unadjusted. The record does not describe a multiplicity plan, such as how the probability of false-positive findings across multiple comparisons or outcomes would be controlled. The comparisons should therefore be read as separate unadjusted results rather than assumed to form a family of confirmatory tests with a stated error-control procedure.

The primary outcome is reported for the per protocol population. This population may differ from the full randomized population, but the registry record does not describe the criteria used to define it or the reasons participants may have been excluded. The primary endpoint denominators are 150 for test product, 160 for reference product, and 75 for placebo. The record does not provide a participant-flow account that reconciles these denominators with the enrollment of 469.

Missing primary outcome data and their handling are not reported in the registry record. It is not stated whether any outcomes were missing, how missingness was classified, or whether an imputation or sensitivity analysis was used. Those details matter because analyses of incomplete data can depend on assumptions about why observations are missing and how those observations relate to outcomes.

The adverse-event denominators differ from the per protocol denominators. The record does not explain the rules defining the safety population or whether all randomized participants were included in safety summaries. It also does not report interim analyses, a stopping rule, or the original statistical analysis plan. These omissions do not change the posted counts, but they limit assessment of whether the analyses were prespecified and how robust the findings are to analysis-population and missing-data choices.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: group b streptococcus wound infection (1.1%), metastatic malignant melanoma (0.5%), acute congestive heart failure (0.5%), transient ischemic attack (0.5%).

The adverse-event summary lists serious adverse events for 1 of 187 participants at risk in the test-product group, 2 of 189 in the reference-product group, and 1 of 93 in the placebo group. Deaths are recorded as 0 in each group. These are raw counts with their posted at-risk denominators; they are not the same denominators as those used for the primary per protocol outcome.

Other adverse events affected 44 of 187 participants at risk in the test-product group, 50 of 189 in the reference-product group, and 6 of 93 in the placebo group. The registry also lists Group B Streptococcus Wound Infection at 1.1%, Metastatic Malignant Melanoma at 0.5%, Acute Congestive Heart Failure at 0.5%, and Transient Ischemic Attack at 0.5% among the top serious-event terms. The record does not assign those listed terms to particular groups in the posted summary.

These summaries describe the events recorded in the registry; they do not provide event timing, severity grades, relatedness assessments, or a complete narrative of each event. The registry record does not explain whether follow-up duration was the same across groups or how event coding was conducted. Raw adverse-event counts should not be interpreted as a complete comparison of safety without those details and the broader clinical context.

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

The posted primary outcome describes the number of participants with complete clearance by Day 57 in the per protocol population. Test product and reference product each had 71 participants meeting the endpoint, while their denominators differed. The unadjusted recalculated comparison has a risk-difference interval that includes zero and a p-value of 0.601. These results do not demonstrate a clear difference between those groups in this recalculation, but they also do not demonstrate equivalence. Equivalence requires a prespecified margin, which is not reported in the registry record.

The reference-versus-placebo recalculation has an interval entirely on one side of zero and an unadjusted p-value of <0.001. This indicates that the posted per protocol clearance proportions differ under that comparison and calculation. It does not, by itself, establish the size or clinical importance of the difference, nor does it provide information about other outcomes or follow-up beyond Day 57.

The sponsor’s own analysis reports an equivalence ratio and a 90% confidence interval but no p-value. Because the equivalence margin and interpretation of its interval are not reported, the registry entry does not permit a complete assessment of the sponsor’s equivalence claim. Recalculated risk differences and the sponsor’s equivalence analysis answer different statistical formulations and should be kept distinct.

The safety summary records serious adverse events, other adverse events, and deaths by group, but it does not include enough detail to characterize event severity, attribution, timing, or comparative risk comprehensively. The posted evidence is also limited by the per protocol primary analysis and the absence of details about missing data, participant flow, and the original analysis plan. No conclusion should extend beyond the recorded outcomes, populations, and timeframe.

17. Why This Trial Matters Statistically

This trial is statistically useful because its registry record presents three treatment groups and a binary primary endpoint, while also showing how the choice of comparison affects the statistical question. The test-versus-reference comparison is framed as an equivalence analysis by the sponsor, whereas the recalculation reports an unadjusted risk difference. Those are not interchangeable approaches: equivalence depends on a prespecified acceptable range, while a difference test asks whether the data are inconsistent with no difference.

The posted results also illustrate why an estimate should be read with its confidence interval rather than relying only on a point estimate or p-value. The test-versus-reference interval spans zero, and the unadjusted p-value is 0.601. The placebo comparison’s interval lies on one side of zero, with an unadjusted p-value of <0.001. Each result describes a different pair of groups and should not be transferred to another comparison.

Another statistical issue is the distinction between analysis populations. Primary endpoint counts are reported for the per protocol population, while adverse-event counts use different denominators. Without a participant-flow description, a reader cannot determine how those populations relate to everyone enrolled or how exclusions may affect interpretation.

Finally, the planning illustrations show how assumed effect size influences required enrollment: smaller target effects call for larger sample sizes under the stated calculation assumptions. These are not the original design justification and are not evidence of the trial’s power after completion. Together, these points make the record a practical example of interpreting effect measures, uncertainty, equivalence claims, analysis populations, and planning assumptions without conflating them.

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 endpoint is reported only for the per protocol population, and the registry record does not define that population or explain exclusions. Although total enrollment is 469, the primary outcome denominators are smaller and differ by group. No participant-flow information is reported to clarify how the enrolled participants relate to the primary analysis set.

The registry entry does not report missing-outcome counts or the method used to handle missing data. It also does not report the original statistical analysis plan, multiplicity approach, interim analyses, or original sample-size justification. Consequently, the posted recalculations cannot be confirmed as matching the trial’s prespecified analysis, and the planning illustrations should not be mistaken for the trial’s design calculation.

The sponsor’s equivalence-ratio result lacks a reported equivalence margin and an explanation of the interval’s units. That prevents assessment of whether the interval meets a meaningful equivalence criterion. The recalculated comparisons are unadjusted, so they do not account for covariates or any multiplicity strategy.

The primary outcome is limited to complete clearance from baseline to Day 57. The record does not report longer-term clearance, partial response, lesion-count changes, or further endpoint assessment. Safety information is also limited: the registry gives counts of serious and other adverse events and deaths, but not timing, severity, relatedness, or detailed group attribution for the listed serious-event terms. These limitations restrict interpretation to the outcomes and details actually recorded.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: To Compare Safety and Efficacy of Perrigo's Drug Compared to an FDA Approved Drug in the Treatment of Actinic Keratosis — NCT02459795.
• Registry record last updated 2021-11-02; status last verified 2021-10.
• Results first posted 2021-01-22.
• 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

NCT02459795 is a completed randomized, double-masked, parallel-group phase 3 study sponsored by Padagis LLC. It enrolled 469 participants with actinic keratosis and compared Ingenol Mebutate (Perrigo), Ingenol Mebutate (Reference), and placebo gel. The recorded study start was 2015-05, and primary completion was 2015-12.

The primary outcome was the number of participants with complete clearance of actinic keratosis lesions from baseline to Day 57 in the per protocol population. The sponsor-reported analysis compared test product with reference product using Yates correction and an equivalence-ratio parameter. Unadjusted recalculations compare test product and placebo separately with reference product. The registry record does not report the equivalence margin, original sample-size justification, missing-data handling, or multiplicity plan.