Safety and Effectiveness Study of Imiquimod Creams for the Treatment of Actinic Keratoses (AKs): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Effectiveness Study of Imiquimod Creams for the Treatment of Actinic Keratoses (AKs) (NCT00603798), a randomized phase 3 study. The primary outcome is Number of Participants With Complete Clearance of AK Lesions.

2. Clinical Question

The clinical question concerns a defined lesion-clearance outcome at a stated follow-up visit. It is not a question about preventing future actinic keratoses, treating lesions outside the identified treatment area, or comparing long-term outcomes. The registry also lists partial clearance, change in lesion count, and local skin reactions as secondary outcomes; these address related but distinct aspects of the study.

3. Trial Design

The registry describes a phase 3, randomized, triple-masked, parallel-group, placebo-controlled, multicenter study. It lists 490 participants enrolled and marks the study completed. The official title describes six weeks of treatment with imiquimod creams for actinic keratoses. The study description identifies the face or balding scalp as the intended treatment location. The record lists three groups: 3.75% imiquimod cream, 2.5% imiquimod cream, and placebo cream.

For the primary outcome, the registry lists 162 participants in the 3.75% group, 164 in the 2.5% group, and 164 in the placebo group. The outcome is assessed at the end-of-study Week 17 visit. These are the outcome-group denominators recorded for the primary result, not a substitute for details about participant flow, protocol adherence, or the analysis set beyond what the registry states.

The registry says efficacy analyses used the intent-to-treat population. It also describes handling missing primary-outcome observations with last observation carried forward for the primary analysis and taking missed observations as failures for a sensitivity analysis. The description ends while referring to another approach, so any additional missing-data method is not reported in the registry record. The record does not give the trial’s original sample-size assumptions, allocation ratio rationale, or a fuller account of the analysis plan. It also does not specify the people included in the stated triple masking.

The recorded start was 2008-01 and the primary completion was 2008-07. Those registry dates provide context for the study record; they do not establish the duration of follow-up for every participant. The posted primary endpoint is measured at Week 17, while the local-skin-reaction outcome describes an assessment period extending to eight weeks after treatment ended.

4. Participant Flow and Accounting

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

Before assignment: Subjects were screened and had to meet eligibility requirements for randomization. The most frequent reason for screen failure (44 of screen failures) was that the subject did not have between 5 and 20 visible or palpable lesions on either the face or the balding scalp.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Efficacy analyses were conducted on the intent-to-treat (ITT) population. For the primary efficacy variable, imputations were made for missing data points using last observation carried forward (LOCF), primary analysis), taking all missed observations as failure (sensitivity analysis), and using observed cases only (supportive analysis).

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 of AK Lesions, measured over End of Study the Week 17 visit.

The primary endpoint is the number of participants with complete clearance of actinic keratosis lesions at the end-of-study Week 17 visit. The registry defines complete clearance as the absence of clinically visible or palpable actinic keratosis lesions in the treatment area. The count includes all lesions in that area, including lesions that appeared after baseline and subclinical lesions that were not identified at baseline.

This endpoint turns a clinical examination into a binary participant-level outcome: a participant either met the stated complete-clearance definition or did not. Counting participants who meet a prespecified definition can make the result easier to interpret than a change in lesion count alone, because it describes the proportion of a group reaching a particular status. It also means the endpoint discards distinctions among participants who did not reach complete clearance: partial improvement and little or no change are both outside the complete-clearance count.

The endpoint is tied to a particular visit and treatment area. It therefore describes clearance at the recorded assessment, not durable clearance beyond that visit or effects on lesions elsewhere. The registry lists partial clearance and change from baseline in lesion count as secondary outcomes, which provide complementary information about responses that complete clearance alone does not capture. The endpoint’s clinical meaning depends on the registry’s examination-based definition and the handling of missing observations; the record describes imputation approaches but does not give a complete account of every analysis detail.

7. Results Posted in the Registry

• 3.75% Imiquimod Cream: 34.0% (55/162) versus 5.5% (9/164) on control; risk difference 28.5 percentage points (95% CI 20.4 to 36.5), risk ratio 6.19 (3.16–12.10); unadjusted two-proportion z-test p = <0.001.
• 2.5% Imiquimod Cream: 25.0% (41/164) versus 5.5% (9/164) on control; risk difference 19.5 percentage points (95% CI 12.0 to 27.0), risk ratio 4.56 (2.29–9.07); 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.

Number of Participants With Partial Clearance of AK Lesions

• 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:
  • 3.75% Imiquimod Cream: 53.7% (87/162) versus 12.8% (21/164) on control; risk difference 40.9 percentage points (95% CI 31.7 to 50.1), risk ratio 4.19 (2.74–6.41); unadjusted two-proportion z-test p = <0.001.
  • 2.5% Imiquimod Cream: 42.7% (70/164) versus 12.8% (21/164) on control; risk difference 29.9 percentage points (95% CI 20.7 to 39.0), risk ratio 3.33 (2.15–5.16); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for 3.75% Imiquimod Cream than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for 2.5% Imiquimod Cream than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Local Skin Reactions (LSR)

• 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:
  • 3.75% Imiquimod Cream: mean 413.50 versus 188.60 on control; difference 224.90 (95% CI 188.31 to 261.49), standardized effect d = 1.38; z-test p = <0.001.
  • 2.5% Imiquimod Cream: mean 372.00 versus 188.60 on control; difference 183.40 (95% CI 147.95 to 218.85), standardized effect d = 1.15; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for 3.75% Imiquimod Cream than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for 2.5% Imiquimod Cream than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes address related but distinct dimensions of the study. Partial clearance and change in lesion count concern lesion response without requiring complete clearance. Local skin reactions describe treatment-associated reactions over an assessment period that extends to eight weeks after treatment ended. Read together with complete clearance, these outcomes offer a broader picture than a single all-or-none endpoint, but they do not measure the same construct and should not be combined as if they were interchangeable.

The posted secondary results follow a generally consistent pattern in the group summaries: both imiquimod groups have more participants recorded with partial clearance than placebo, and the mean local-skin-reaction scores are higher in the imiquimod groups. The partial-clearance comparisons have unadjusted p values of <0.001. The local-skin-reaction comparisons also have unadjusted p values of <0.001. These summaries complement the primary endpoint by describing partial response and reactions, rather than proving that one outcome explains another.

Secondary findings generally carry less inferential weight when many outcomes or comparisons are considered without a reported multiplicity strategy. Repeated testing can increase the chance of apparently strong findings arising in a collection of analyses even when each individual test uses a conventional threshold. The registry lists no reported analyses for these secondary outcomes, and it does not report an adjustment procedure or a formal hierarchy that would establish which secondary questions were confirmatory. Their p values should therefore be treated as exploratory recalculations, not as independent confirmation of the primary result.

The secondary results also do not resolve the limitations of the primary assessment. Partial clearance does not tell how long clearance lasts, and lesion-count change is not equivalent to complete clearance. A local-reaction score reflects a different kind of outcome and should be interpreted in its own measurement context. Taken together, the secondary endpoints add descriptive context, while leaving uncertainty about long-term outcomes, clinical importance, and the balance of benefits and harms.

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

• Number of Participants With Partial Clearance of AK Lesions
• Percent Change From Baseline in AK Lesion Count
• Local Skin Reactions (LSR)

9. Statistical Interpretation

10. Statistical Methods Explained

Clinical trial outcomes can be summarized in different ways depending on whether the result is a count, a proportion, or a measurement on a continuous scale. The primary outcome is binary at the participant level: each participant either met the complete-clearance definition or did not. A risk difference expresses the difference between the proportions meeting that definition in two groups. It uses the same scale as the outcome proportions, so a positive value in an imiquimod-versus-placebo comparison means a higher observed proportion in the imiquimod group. The posted comparisons use placebo as the reference group.

The recalculated risk-difference estimates and their confidence intervals are unadjusted. “Unadjusted” means the comparison is based on the posted group summaries rather than a model controlling for other participant characteristics or study factors. Randomization supports a fair comparison in expectation, but the registry record does not report a covariate-adjusted primary analysis. The recalculations should not be mistaken for a complete reconstruction of the trial’s original statistical plan.

What does a p value say?

A p value measures how unusual data at least as incompatible with a null hypothesis would be if that null hypothesis and the calculation’s assumptions held. For the primary comparisons, the posted unadjusted p values are <0.001. This is evidence against a zero-difference null under the calculation used. It is not the probability that the null hypothesis is true, the probability that the result is due to chance, or a measure of clinical importance. It also does not account automatically for the many outcomes or comparisons that may be considered.

Why use a confidence interval?

A confidence interval describes the uncertainty around an estimated effect under a specified method. For a risk difference, the interval gives a range of values compatible with the observed data and method. An interval that excludes zero is consistent with a nonzero difference under that method, but does not remove uncertainty about the true effect. Its width reflects statistical precision: narrower intervals indicate less sampling uncertainty, while wider intervals indicate more. Confidence intervals do not capture every source of uncertainty, such as bias from missing data, limitations in outcome measurement, or differences between the trial population and other populations.

How should binary outcomes be read?

For a binary endpoint, the group count and group denominator together describe how often the event was recorded. The number with complete clearance is not a measure of how much each participant improved; it records whether the all-or-none endpoint definition was met. A risk difference retains an absolute scale, whereas relative measures such as risk ratios and odds ratios describe a comparison on different scales. The registry record includes recalculated risk ratios and odds ratios, but the clearest main interpretation is the absolute difference in the chance of meeting the endpoint. Relative measures should not be confused with percentage-point differences.

For continuous outcomes, the registry reports group means and standard deviations. A mean difference compares average values between groups, while the standard deviation describes variation among individual measurements within a group. The local skin reactions result is an area-under-the-curve measure expressed in units on a scale multiplied by days. It is not the same kind of outcome as complete clearance. Differences in scale and direction matter when interpreting these results, and a larger average reaction score is not automatically a benefit.

Why can over-dispersion matter?

General statistical principle: a model that assumes a particular amount of variability can give misleading standard errors if real outcomes vary more than that assumption allows. Over-dispersion means the observed variability is greater than the model expects. It can make confidence intervals too narrow and p values too small if the analysis does not account for the extra variability. The registry record does not report a model-based analysis of the primary binary outcome or say whether over-dispersion was assessed, so this is general context rather than a claim about the trial’s analysis.

What does the intent-to-treat description imply?

The registry states that efficacy analyses used the intent-to-treat population. In general, an intent-to-treat approach aims to analyze participants according to their randomized groups, regardless of treatment adherence, preserving the comparison created by random assignment. How this was implemented depends on participant availability and missing-data rules. The record says last observation carried forward was used for the primary efficacy analysis and that missed observations were treated as failures in a sensitivity analysis. These choices can affect the estimated group outcomes. The available description does not fully state the additional approach mentioned in the record, nor does it describe the extent or pattern of missingness.

All inferential quantities described for the group comparisons are unadjusted recalculations from posted summary statistics. The registry’s reported-analyses fields are empty for the listed outcomes. This limits what can be said about the sponsor’s actual inferential methods, prespecified contrasts, or adjustment strategy. The record does not report whether analyses were conducted at interim points or how the original study’s sample size was justified.

11. Confidence Intervals and Precision

The primary risk-difference intervals are informative about sampling precision: each lies above zero, while still covering a range of possible effect sizes. The intervals therefore support a positive observed difference under the recalculation method without identifying a single exact value as certain. Their width is a reminder that estimates remain uncertain even when a p value is small.

Precision and validity are different. A narrow interval can indicate low sampling uncertainty under a statistical method, but it cannot correct bias or make an endpoint more clinically meaningful. The primary result depends on how complete clearance was assessed and how missing observations were handled. The registry describes last observation carried forward for its primary efficacy analysis and a sensitivity analysis treating missed observations as failures, but the record does not provide enough detail to assess every missing-data assumption or the extent of missingness.

The posted intervals are unadjusted recalculations from the summary data, not a substitute for a fully reported prespecified analysis. They do not account for testing across multiple outcomes unless an adjustment is explicitly used; no multiplicity adjustment is reported in the registry record. Their interpretation is therefore conditional on the calculation and on treating these comparisons as considered on their own.

These intervals quantify uncertainty in the group comparison, not the probability that a future study will produce the same estimate. Replication, differences in populations and settings, and the trial’s outcome-assessment procedures all matter for judging how broadly the results apply. The intervals also do not establish persistence beyond the Week 17 assessment.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design assumptions. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. For these binary and continuous outcomes, the estimates are participants per arm; they are not total event counts. The time-to-event convention is not relevant to the outcomes reported for this study.

The 80% power column describes the estimated number of participants per arm under those assumptions for a design that would have an 80% probability of detecting the specified effect if that effect were the true one. The 90% power column uses a higher target probability of detection and consequently generally requires more participants per arm. Power is a design property under assumed conditions, not a measure of how convincing or important an observed result is.

The rows for planning at 100%, 75%, and 50% of the observed effect illustrate how the estimated requirement changes when the target effect is smaller. Smaller effects need more participants because they are harder to distinguish from random variation. The calculations are based on effect sizes observed in this study, so they are sensitive to how large those observed effects are and should not be treated as a universal design recommendation.

This is not observed power. The registry does not report the trial’s original sample-size justification or the assumptions used to plan enrollment. The planning figures therefore cannot establish whether the study was planned with these assumptions, nor do they replace a forward-looking design calculation based on a clinically chosen effect and appropriate study-specific assumptions.

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 = 0.055; treatment proportion p₁ = 0.340; average p̄ = 0.197.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5627 = 1.1028.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5255 = 0.4422.
4. n = (1.1028 + 0.4422)² / (0.2846)² = 29.5, rounded up to 30 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 <- 0.0548780487804878                          # control proportion
p1 <- 0.339506172839506                          # 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(603798)
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 = 30 (80% power), 39 (90% power)
 75% of observed effect: n per arm = 46 (80% power), 61 (90% power)
 50% of observed effect: n per arm = 85 (80% power), 113 (90% power)
power.prop.test: 29.5 
Simulated power at n = 30 per arm: 0.846 (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. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity adjustment, a prespecified hierarchy among the primary and secondary outcomes, or a strategy for controlling the overall chance of false-positive findings across comparisons. The primary endpoint includes two comparisons with placebo, and additional secondary outcomes are listed. When several hypotheses are tested, considering each p value in isolation can overstate the strength of the overall evidence. This does not mean a particular finding is false; it means the unadjusted p values do not address the full family of analyses.

The record lists no reported analyses for the primary outcome or the posted secondary outcomes. The estimates and tests described in the statistical interpretation are recalculations from the posted group summaries. They do not reveal whether the original investigators used a different model, prespecified analysis population, or adjustment procedure. Those details are not reported in the registry record.

For missing primary-outcome data, the registry says the efficacy analysis used the intent-to-treat population. It describes last observation carried forward for the primary analysis and treating all missed observations as failures in a sensitivity analysis. The record’s description then begins to mention another method but is incomplete. The further approach is not reported in the registry record. The number and timing of missing observations, reasons for missingness, and results of the described sensitivity analyses are also not reported in the registry record.

Missing-data methods rely on assumptions about what unobserved outcomes would have been. Last observation carried forward assumes, in effect, that the last recorded status can stand in for a later missing assessment. Treating missing observations as failures makes a different assumption for this endpoint. Neither method can be evaluated fully without information about missingness and the complete analysis results. The availability of a sensitivity analysis is useful, but the registry record does not provide enough detail to determine how sensitive the conclusions were to alternative assumptions.

The trial’s original sample-size justification, interim-analysis plan, and detailed statistical analysis plan are not reported in the registry record. These omissions limit assessment of prespecification and selective reporting, independently of whether the recalculated comparisons are statistically notable.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

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: breast cancer (0.6%), surgery (0.6%), dyspnea (0.6%), hip fracture (0.6%), arthralgia (0.6%).

The registry reports serious adverse events affecting 10 participants in the 3.75% imiquimod group, 5 in the 2.5% group, and 3 in the placebo group. The corresponding group counts at risk are 162, 164, and 164. These figures describe participants with serious adverse events as recorded in the safety results; they do not by themselves establish that an event was caused by study cream.

The record also lists other adverse events affecting 39 participants in the 3.75% group, 29 in the 2.5% group, and 2 in the placebo group, with the same group-specific at-risk counts as recorded for these results. The listed serious-event terms include breast cancer, surgery, dyspnea, hip fracture, arthralgia, and wound infection staphylococcal, each reported as 0.6%. The registry does not provide enough context in these figures to determine the relationship of each event to treatment.

Deaths are not reported in the registry record. Adverse-event counts are descriptive safety data, not randomized estimates of causality. They should be considered alongside event definitions, follow-up, exposure, and clinical review, details that are not fully available in this record. The counts alone do not establish comparative safety.

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

The posted primary result describes the number of participants in each group who met the registry’s complete-clearance definition at the Week 17 visit. More participants in each imiquimod group than in the placebo group were recorded as having complete clearance. The unadjusted recalculated comparisons and their intervals summarize the observed group differences, but they do not establish an exact effect or guarantee that the same result would occur in another study.

The finding applies to the study’s enrolled population, treatments, lesion definition, treatment area, and assessment visit. It does not show whether clearance persisted after the recorded visit, whether lesions outside the treatment area changed, or whether the results apply to people who would not have met the trial’s eligibility criteria. Further eligibility and participant-flow details are not reported in the registry record.

Complete clearance is a stringent binary outcome: it records whether a participant met the no-visible-or-palpable-lesions definition. It does not describe the amount of improvement among participants who did not meet that definition. The secondary outcomes offer related information about partial clearance, lesion count, and local skin reactions, but each has a different interpretation. The registry’s safety counts are also descriptive and do not establish that reported events were caused by treatment.

A small p value is not proof of clinical importance, and statistical evidence of a group difference is not, on its own, a complete assessment of benefit and harm. The record does not report a multiplicity strategy, a full analysis plan, or complete details of missingness and sensitivity analyses. Those gaps should be kept in view when weighing the recalculated statistical evidence.

The result is best understood as a comparison of recorded Week 17 clearance outcomes across randomized groups, not as a conclusion about long-term effectiveness, individual response, or treatment choice. Determining clinical relevance would require context beyond these group summaries, including the importance of the outcome to patients and a fuller account of benefits, harms, and durability.

17. Why This Trial Matters Statistically

This study illustrates why a clearly defined endpoint matters. Complete clearance is not simply a lower lesion count; it requires no clinically visible or palpable lesions in the treatment area, including new or subclinical lesions. The rule gives the outcome a concrete meaning, while also making it an all-or-none summary that does not capture the degree of partial response.

It also illustrates the value of separating absolute comparisons from tests of statistical significance. A risk difference places the group contrast on the scale of the outcome itself, and a confidence interval conveys uncertainty around that contrast. The p value addresses a different question and cannot stand in for the size or precision of the estimated difference. Considering these quantities together helps avoid reducing interpretation to a threshold alone.

Randomized, parallel-group, placebo-controlled design supports a direct comparison between assigned groups, but interpretation still depends on analysis decisions. The registry describes an intent-to-treat population and more than one approach to missing primary data, while leaving part of the missing-data description incomplete. That makes it useful to distinguish the posted group summaries and recalculations from a fully documented prespecified analysis.

Finally, the trial has several outcomes and comparisons. The secondary results can add context, but without a reported multiplicity strategy they should not be treated as separate confirmatory proof. This is a practical example of how sound statistical interpretation combines endpoint definition, effect estimates, uncertainty, missing-data assumptions, and the scope of the analysis rather than relying on a single result.

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 registry record provides limited detail about eligibility, participant flow, adherence, and the exact treatment application schedule. Although the official title describes six weeks of treatment and the study description refers to the face or balding scalp, fuller protocol details are not reported in the registry record. These omissions make it difficult to judge how closely the posted results reflect treatment as planned or how broadly they apply.

The primary endpoint is assessed at Week 17, and the registry does not report longer-term clearance results. The posted outcome therefore cannot establish durability. Complete clearance also compresses a range of possible responses into a binary classification. Partial clearance and lesion-count outcomes provide additional information, but the registry record lists no reported analyses for them.

The analysis record is incomplete. It states that efficacy analyses used the intent-to-treat population and identifies last observation carried forward as the primary missing-data method, with missed observations treated as failures in a sensitivity analysis. The description of a further method is truncated. Missing-data counts, reasons, and sensitivity-analysis results are not reported in the registry record. The lack of a reported multiplicity strategy and detailed statistical plan also limits assessment of prespecification.

The comparisons discussed are unadjusted recalculations from posted group summaries. They do not include covariate adjustment, and the registry lists no reported analyses for the outcomes. The original sample-size justification and interim-analysis plan are not reported in the registry record. Finally, the safety summaries are counts of participants with recorded events; they do not establish causation or provide a complete account of the clinical context of each event.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Effectiveness Study of Imiquimod Creams for the Treatment of Actinic Keratoses (AKs) — NCT00603798.
• Registry record last updated 2010-06-29; status last verified 2010-06.
• Results first posted 2010-06-22.
• 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

The registry describes a completed phase 3, randomized, triple-masked, parallel, placebo-controlled, multicenter study of 3.75% imiquimod cream, 2.5% imiquimod cream, and placebo cream for actinic keratoses. Enrollment was 490. The official title describes six weeks of treatment, and the primary outcome was complete clearance at the end-of-study Week 17 visit.

The posted primary counts were 55 participants with complete clearance in the 3.75% group, 41 in the 2.5% group, and 9 in the placebo group. The unadjusted recalculated comparisons against placebo have p values of <0.001. Secondary outcomes address partial clearance, lesion-count change, and local skin reactions. The registry also reports serious and other adverse-event counts.

The available record does not report a complete statistical analysis plan, a multiplicity strategy, the original sample-size justification, or the full missing-data description. Interpret the recalculated comparisons as statistical summaries of posted results, not as a substitute for a complete prespecified analysis or a conclusion about long-term outcomes.