A Study of Equivalence of Generic Ingenol Mebutate Gel 0.05% and Picato Gel 0.05% in Subjects With Actinic Keratosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Equivalence of Generic Ingenol Mebutate Gel 0.05% and Picato Gel 0.05% in Subjects With Actinic Keratosis (NCT02654769), a randomized phase 3 study. The primary outcome is Primary Efficacy Outcome Measure.

2. Clinical Question

The study had two related aims: to evaluate safety and therapeutic equivalence between the generic product and Picato, and to establish superiority of both active products over vehicle for efficacy. These are distinct statistical questions. Equivalence asks whether the difference between the two active treatments is sufficiently small according to a prespecified margin. Superiority asks whether an active treatment differs from vehicle in the direction of greater clearance. The equivalence margin is not reported in the registry record, so the sponsor’s equivalence result cannot be fully judged from the posted information alone.

The primary outcome was complete clearance, defined as having no clinically visible actinic keratosis lesions in the treatment area at the Week 8 visit. The secondary outcome considered partial clearance, defined as at least 75% reduction in lesion count. Both outcomes focus on the treatment area and the per-protocol population. The registry record describes the condition and treatment area but does not report further eligibility details or the treatment regimen.

3. Trial Design

The registry record describes a completed, randomized, Phase 3, multicenter, parallel-group, vehicle-controlled study. Enrollment was 441. The official title calls the study double-blind, while the registry’s masking classification is quadruple. The record does not identify which specific groups of people were masked, so the masking classification should not be expanded into assumptions about who knew treatment assignment.

The three groups were Picato gel, 0.05%, generic ingenol mebutate gel, 0.05%, and vehicle gel. Picato was designated the reference listed drug, the generic product the test treatment, and the vehicle the vehicle control. The stated objective was to evaluate safety and therapeutic equivalence between the generic and reference products and to assess whether both products were superior to vehicle for efficacy. The primary outcome was assessed at 8 weeks.

The registry record lists the study start as 2015-02 and primary completion as 2015-09, with status completed. It does not report the randomization sequence method, allocation concealment, details of the study sites, treatment application schedule, or the original sample-size justification. It also does not report whether interim analyses were planned or conducted. Those design details should not be inferred from the randomized and masked classifications.

Primary efficacy results are reported for the per-protocol population. The efficacy denominators were 131 for Picato, 135 for generic ingenol mebutate, and 132 for vehicle. The safety denominators differed: 149 for generic ingenol mebutate, 149 for Picato, and 143 for vehicle. The registry record does not explain the difference between these analysis populations or the reasons participants were not included in the per-protocol efficacy results.

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.

Population: Subjects in Modified Intent-to-Treat Population

6. Primary Endpoint

The registry lists the primary outcome as Primary Efficacy Outcome Measure, measured over 8 weeks.

The primary endpoint counts participants in the per-protocol population who achieved complete clearance of actinic keratosis lesions in the treatment area at the 8-week visit. Complete clearance was defined as having zero clinically visible lesions in that area. The outcome is binary for each participant: complete clearance was either present or absent at the specified assessment.

This endpoint addresses a direct efficacy question: whether the treated area was free of clinically visible lesions at the assessment visit. It is stricter than partial clearance, which is the secondary outcome and allows some lesions to remain if the lesion count has fallen by at least 75%. The registry reports the primary result as participant counts by treatment group, alongside the group denominators.

Using a prespecified assessment time and a defined lesion-clearance threshold makes the outcome interpretable as a comparison between groups at that visit. However, the endpoint does not describe outcomes beyond 8 weeks, changes outside the treatment area, or other measures of disease course. The registry record does not report how lesion assessments were standardized, whether assessors were independently trained, or how missing endpoint assessments were handled. These details would help assess how consistently the endpoint was measured and how participants without a recorded Week 8 result were treated in the analysis.

7. Results Posted in the Registry

• Generic Ingenol Mebutate: 36.3% (49/135) versus 38.2% (50/131) on control; risk difference -1.9 percentage points (95% CI -13.5 to 9.7), risk ratio 0.95 (0.70–1.30); unadjusted two-proportion z-test p = 0.752.
• Vehicle Foam: 6.1% (8/132) versus 38.2% (50/131) on control; risk difference -32.1 percentage points (95% CI -41.4 to -22.8), risk ratio 0.16 (0.08–0.32); unadjusted two-proportion z-test p = <0.001.

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.

The Percentage of Subjects in the PP Population in Each Treatment Group With Partial Clearance (as Having at Least 75% Reduction in the Number of Clinically Visible AK Lesions) in theTreatment Area at the Week 8 Visit.

• 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:
  • Generic Ingenol Mebutate: 61.5% (83/135) versus 64.1% (84/131) on control; risk difference -2.6 percentage points (95% CI -14.3 to 9.0), risk ratio 0.96 (0.80–1.15); unadjusted two-proportion z-test p = 0.656.
  • Vehicle Foam: 15.9% (21/132) versus 64.1% (84/131) on control; risk difference -48.2 percentage points (95% CI -58.5 to -37.9), risk ratio 0.25 (0.16–0.37); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Generic Ingenol Mebutate 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 proportion with the event is statistically lower for Vehicle Foam than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary endpoint assesses partial clearance, defined as at least 75% reduction in the number of clinically visible lesions in the treatment area at Week 8. Its overall pattern resembles the primary endpoint: the two active-treatment groups are close to one another in the posted results, while vehicle has a lower partial-clearance outcome. The secondary outcome therefore provides a related view of lesion response using a less stringent threshold than complete clearance.

That resemblance does not make the secondary outcome an independent confirmation of the primary result. The measures use the same clinical setting, treatment groups, assessment time, and per-protocol population, and they are related definitions of clearance. Participants who meet the stricter complete-clearance definition may also contribute to the broader partial-clearance measure. The secondary outcome can add context about a different degree of lesion reduction, but it does not answer the same question as complete clearance.

The registry reports a sponsor equivalence analysis for the active-treatment comparison on the secondary endpoint, as well as unadjusted recalculations for the contrasts. However, the multiplicity plan is not reported in the registry record. When multiple outcomes and comparisons are examined, unadjusted results carry less weight as confirmatory evidence because the chance of at least one apparently notable result can increase across repeated testing. The registry does not state whether the secondary endpoint was prespecified as confirmatory, how it was ranked relative to the primary endpoint, or whether multiplicity was controlled.

The secondary results should therefore be read as supportive context rather than as a separate definitive basis for an equivalence conclusion. As with the primary endpoint, evaluating equivalence requires the prespecified margin and the sponsor’s decision rule, neither of which is reported in the registry record. The direction of the overall pattern can be described, but claims about confirmation or formal success require details not available in the record.

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

• The Percentage of Subjects in the PP Population in Each Treatment Group With Partial Clearance (as Having at Least 75% Reduction in the Number of Clinically Visible AK Lesions) in theTreatment Area at the Week 8 Visit.

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas are relevant to reading these results. The registry gives participant counts, group denominators, sponsor-reported equivalence results, and simple unadjusted re-calculations. Those elements answer related but not interchangeable questions. The calculations based on posted summaries are descriptive comparisons; the sponsor’s reported analysis is the analysis identified by the registry as an equivalence analysis.

What does a risk difference describe?

A risk difference compares the proportion of participants with an outcome in one group with the proportion in a reference group. A value below zero means the outcome proportion is lower in the first group as oriented in the comparison; a value above zero means it is higher. The sign depends on which group is treated as the reference. For the primary outcome, the generic-versus-Picato re-calculation is -0.019. The vehicle comparison is also negative because the vehicle group has a lower complete-clearance proportion than the active reference group in the orientation used for that comparison. A risk difference is an absolute contrast, rather than a relative measure such as a risk ratio.

What does a confidence interval convey?

A confidence interval describes the uncertainty around an estimated contrast under the statistical method used. A narrower interval indicates greater precision, while a wider interval leaves a broader range of effect sizes compatible with the data and method. For a conventional superiority question, an interval that includes zero does not establish a difference at the corresponding two-sided significance threshold. For equivalence, the key question is different: the interval must lie entirely within prespecified acceptable bounds. A result that is not statistically different from zero does not, by itself, demonstrate equivalence. Since the equivalence bounds are not reported in the registry record, the sponsor’s equivalence conclusion cannot be checked against them from the posted record.

Why is the equivalence analysis distinct?

Equivalence testing is designed to assess whether the difference between treatments is small enough to fall within a clinically and statistically justified range. That range must be specified before interpreting the results. The sponsor analysis is identified as Fisher Exact and reports a 90% Wald’s confidence interval, with a point estimate of -1.87 and limits of -12.37 and 8.63. The registry also reports p < 0.001 for this analysis. The record does not provide the equivalence margin or additional detail explaining the role of that p-value. Consequently, the reported interval and label can be described, but the statistical decision rule cannot be independently reconstructed.

How should the re-calculations be used?

The re-calculations are simple, unadjusted analyses based on the posted group summaries. They are useful for showing the size and direction of a crude contrast and how uncertain that contrast is under the stated calculation. They do not reproduce any unreported covariate adjustment, missing-data procedure, stratification, or other feature of the sponsor’s analysis. Where the sponsor’s result and a simple re-calculation differ, the sponsor’s own analysis takes precedence. In this record, the sponsor reported an equivalence analysis for the active treatments, while the re-calculation is an unadjusted risk-difference comparison; they should not be treated as identical analyses.

What does randomization contribute?

In general, random allocation is used to reduce systematic differences between groups at baseline, so that outcome contrasts can be interpreted as comparisons associated with assigned treatments, subject to execution, measurement, and analysis limitations. The registry classifies this study as randomized, but does not report the sequence-generation method, allocation concealment, or baseline balance information in the registry record for these results. No additional protections or adjustments should be assumed.

The per-protocol population is the population specified for the primary and secondary efficacy outcomes. In general, a per-protocol analysis includes participants meeting protocol-related criteria, but the record does not describe the exact criteria or exclusions used. Per-protocol results can differ from results among all randomized participants if exclusions are related to treatment, adherence, outcome availability, or prognosis. The record does not provide an intention-to-treat analysis or enough information to assess those possibilities.

The p-values for the recalculated vehicle contrasts are unadjusted. They address each contrast individually under the calculation used, and do not account for the fact that several comparisons and outcomes are reported. The registry record does not report a multiplicity strategy. The p-values therefore should not be treated as if they were adjusted for all planned comparisons or as proof that every analysis was prespecified.

11. Confidence Intervals and Precision

Precision is reflected in the range of values compatible with an estimate under its confidence-interval method. For the unadjusted generic-versus-Picato primary comparison, the risk-difference estimate is -0.019 and the interval runs from -0.135 to 0.098. The interval spans zero and includes effects in either direction. It therefore leaves substantial uncertainty about the direction and size of the simple unadjusted contrast. It does not establish equivalence, because an equivalence assessment also requires prespecified margins.

The sponsor’s own analysis reports a point estimate of -1.87 and a 90% confidence interval from -12.37 to 8.63. This is the registry’s reported equivalence analysis and takes precedence over the simple re-calculation when describing the sponsor’s conclusion. However, the equivalence margin is not reported in the registry record. Without it, the interval’s position relative to the sponsor’s decision bounds cannot be assessed independently.

The vehicle comparison has a different precision pattern. For generic ingenol mebutate versus vehicle, the unadjusted risk-difference interval runs from -0.414 to -0.229. This interval does not include zero and is positioned below zero in the stated comparison. That provides a more precise indication of the direction of the difference than the active-versus-active re-calculation, while still not addressing unreported analysis choices or missing-data handling.

Confidence intervals are not guarantees that the true effect lies within the displayed limits. They express uncertainty conditional on the data and method used. The available efficacy denominators are 131, 135, and 132 in the per-protocol groups; the safety denominators are different. The registry record does not explain the population differences, which also limits a complete assessment of precision and applicability across outcomes.

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 the study’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. These assumptions describe the illustration only; the original trial’s sample-size assumptions are not reported in the registry record.

For these binary outcomes, the planning figures are participants per arm. They are not total event counts. The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the chosen effect under the stated assumptions, if that effect and model are appropriate. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are planning concepts, not probabilities that the observed trial result is correct.

The rows refer to planning for 100%, 75%, or 50% of the observed effect. Smaller target effects require more participants per arm to detect, because subtle differences are harder to distinguish from random variation. The contrast matters as well: the observed active-versus-vehicle difference is much larger than the observed generic-versus-Picato difference, so the illustrative participant requirements differ substantially. For the primary active comparison, even the row based on 100% of the observed effect gives 10,472 participants per arm for 80% power and 14,018 for 90% power. The vehicle comparison’s corresponding figures are 26 and 33.

These are not observed power. They are hypothetical planning estimates calculated from the observed effect and stated assumptions. They do not demonstrate that the completed study was adequately powered for its original objectives, and they do not account for design details that 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.382; treatment proportion p₁ = 0.363; average p̄ = 0.372.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6837 = 1.3400.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6835 = 0.5753.
4. n = (1.3400 + 0.5753)² / (-0.0187)² = 10,471.2, rounded up to 10,472 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 <- 0.381679389312977                          # control proportion
p1 <- 0.362962962962963                          # 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(2654769)
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 = 10,472 (80% power), 14,018 (90% power)
 75% of observed effect: n per arm = 18,664 (80% power), 24,985 (90% power)
 50% of observed effect: n per arm = 42,099 (80% power), 56,358 (90% power)
power.prop.test: 10471.2 
Simulated power at n = 10,472 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.

14. Analyses Reported by the Sponsor

The registry reports a sponsor analysis for the comparison of generic ingenol mebutate with Picato. It identifies the method as Fisher Exact, gives a 90% Wald’s confidence interval, and labels the analysis as equivalence. The reported estimate is -1.87, with a 90% interval from -12.37 to 8.63, and p < 0.001.

The simple re-calculation from the posted primary counts estimates a risk difference of -0.019, with an interval from -0.135 to 0.098 and an unadjusted p-value of 0.752. These figures are not directly interchangeable with the sponsor’s result: the re-calculation is an unadjusted risk-difference analysis, while the sponsor’s result is identified as the equivalence analysis. The sponsor’s own analysis takes precedence when describing the sponsor-reported equivalence result.

The record does not report the equivalence margin, the detailed analysis specification, or enough information to reconstruct the sponsor’s decision rule. The reported interval therefore cannot be evaluated against the margin using the registry record alone. The reported p-value is listed with the equivalence analysis, but its role is not explained sufficiently to treat it as a conventional test of no difference. The simple re-calculation can illustrate the posted summaries, but it cannot replace missing details of the sponsor’s analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies one primary efficacy outcome and one secondary outcome, each assessed at 8 weeks in the per-protocol population. It also includes comparisons of each active treatment with vehicle and an active-treatment equivalence analysis. The record does not report a multiplicity adjustment or a testing hierarchy across these outcomes and comparisons.

Multiplicity matters because repeated statistical tests create more opportunities for a result to appear notable by chance. In general, a prespecified approach can define which comparison is primary, whether subsequent tests are conditional on earlier results, or how significance thresholds are adjusted. The registry record does not state whether such an approach was used. The re-calculated p-values are unadjusted and should be interpreted as individual comparisons, not as an overall error-controlled set of findings.

Missing-data handling is also not reported in the registry record. The per-protocol efficacy denominators are 131 for Picato, 135 for generic ingenol mebutate, and 132 for vehicle, while the safety denominators are 149, 149, and 143, respectively. The record does not explain why the denominators differ, whether any Week 8 outcomes were missing, how participants were excluded from the per-protocol population, or how missing assessments were handled. No imputation method or sensitivity analysis is described.

The primary and secondary outcomes are reported for the per-protocol population. The registry does not report an intention-to-treat efficacy analysis or details of the protocol criteria used to define the per-protocol group. These omissions limit assessment of how exclusions and missing data may have affected the results. The original statistical analysis plan, including any interim analysis procedures, is not reported in the registry record, so those elements cannot be inferred from the posted outcome summaries.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The safety results list zero serious adverse events in each group: the at-risk denominators are 149 for generic ingenol mebutate, 149 for Picato, and 143 for vehicle. The record also lists zero deaths in each group. No serious adverse-event terms are listed.

For other adverse events, the registry reports 18 affected participants in the generic group, 29 in the Picato group, and 17 in the vehicle group, using the same group-specific safety denominators. The record does not provide event descriptions, severity classifications for these other events, timing, relatedness assessments, or details about whether participants could contribute more than one event. The figures are participant counts, not a complete account of event frequency or clinical significance.

Zero recorded serious adverse events in these groups should be read as the posted observation during the reported safety assessment, not as proof that serious events cannot occur. The registry record does not report the duration or completeness of safety follow-up beyond the study’s 8-week efficacy timeframe, nor does it provide further detail about ascertainment. Safety interpretation is therefore limited to the counts and categories recorded.

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

The registry results describe a randomized comparison of two active products and vehicle for actinic keratosis on the trunk or extremities. The primary outcome was complete clearance in the treatment area at 8 weeks among participants in the per-protocol population. The posted counts show that the two active groups had similar numbers of participants with complete clearance, while the vehicle group had fewer. The unadjusted re-calculations likewise show a larger separation for active treatment versus vehicle than for generic ingenol mebutate versus Picato.

The active-treatment comparison requires particular care. A failure to show a conventional difference is not proof of equivalence. Equivalence is a separate claim that depends on a prespecified margin and an analysis demonstrating that the interval falls within that margin. The sponsor’s result is labeled as an equivalence analysis, but the margin is not reported in the registry record. The sponsor analysis takes precedence over the simple re-calculation, yet its decision criterion cannot be independently assessed from the posted information.

The reported results apply to the stated treatment area, endpoint definition, assessment visit, and analysis population. They do not establish outcomes beyond 8 weeks, effects in other populations or anatomical areas, or outcomes not reported in the registry. The record also does not provide enough information to assess missing-data procedures, the exact per-protocol criteria, or the multiplicity plan.

The safety record reports no serious adverse events or deaths in the listed groups and gives counts for other adverse events. These counts do not describe the event details or establish absence of risk. Overall, the registry supports a description of the posted trial results and their precision, but several design and analysis details needed for a complete independent appraisal are not reported in the registry record.

18. Why This Trial Matters Statistically

This trial raises a central statistical distinction in generic-drug comparisons: similarity is not the same as demonstrated equivalence. A conventional test that fails to find a difference does not establish that two products are close enough. Equivalence requires a margin chosen in advance, along with an interval assessed against that margin. The registry labels the sponsor’s active-treatment analysis as equivalence, but does not report the margin, which prevents independent evaluation of the key criterion.

The contrast with vehicle illustrates why the comparator and statistical question matter. The posted active-versus-vehicle comparisons show a clear difference in the observed complete-clearance counts, while the active-versus-active comparison is a much narrower question about whether the products are sufficiently alike. These questions require different interpretations and should not be collapsed into a single statement about whether an intervention is effective.

The record also shows how population definitions affect interpretation. Efficacy is reported in a per-protocol population, whereas safety uses different denominators. Without the protocol criteria, missing-data procedures, or a corresponding intention-to-treat result, readers cannot fully assess how population selection may have influenced the efficacy comparison.

Finally, the planning illustrations demonstrate that sample-size needs depend strongly on the effect chosen for detection and on the specific comparison. They are not a retrospective measure of whether the trial had adequate power, nor do they replace the original design assumptions. The absence of those original assumptions, alongside the missing equivalence margin and multiplicity plan, makes careful separation of posted results from unreported design choices especially important.

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.

Important details for independently interpreting the results are not reported in the registry record. The equivalence margin is absent, so the sponsor’s equivalence interval cannot be assessed against the required bounds. The original sample-size justification and assumptions are also not reported, and the planning illustrations based on observed effects should not be mistaken for that original justification.

The registry does not describe the randomization sequence, allocation concealment, or which groups were masked, despite classifying masking as quadruple and calling the study double-blind in its official title. It does not give the per-protocol criteria or explain the difference between efficacy and safety denominators. Reasons for exclusion from the efficacy population, missing Week 8 outcomes, and any method for handling missing data are not reported.

The multiplicity strategy, analysis hierarchy, and any adjustments for multiple outcomes or comparisons are not reported. The sponsor’s detailed analysis specification is also not available, and the reported equivalence p-value is not explained. The re-calculations are unadjusted and rely on posted summary statistics; they cannot account for unreported modeling, adjustment, or analysis choices.

The primary and secondary outcomes are both assessed at 8 weeks and concern clearance within the treatment area. Longer-term outcomes and other measures are not reported in the registry record. Safety results provide counts but not detailed event descriptions, severity, relatedness, or additional follow-up information. These limitations do not alter the posted counts, but they restrict the conclusions that can be drawn from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Equivalence of Generic Ingenol Mebutate Gel 0.05% and Picato Gel 0.05% in Subjects With Actinic Keratosis — NCT02654769.
• Registry record last updated 2020-05-12; status last verified 2020-04.
• Results first posted 2020-05-12.
• 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

NCT02654769 is a completed randomized, multicenter, parallel-group Phase 3 study of generic ingenol mebutate gel, 0.05%, Picato gel, 0.05%, and vehicle for actinic keratosis on the trunk or extremities. Enrollment was 441; the registry lists a study start of 2015-02 and primary completion of 2015-09.

The primary outcome was complete clearance at 8 weeks in the per-protocol population. The registry also reports partial clearance as a secondary outcome and safety counts for serious and other adverse events. The sponsor’s active-treatment analysis is labeled as an equivalence analysis, while the posted re-calculations are unadjusted comparisons of summary statistics. The equivalence margin, original sample-size justification, multiplicity plan, and missing-data procedures are not reported in the registry record.