A Clinical Trial of PepCan to Two Therapy Arms for Treating Cervical High-Grade Squamous Intraepithelial Lesions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Clinical Trial of PepCan to Two Therapy Arms for Treating Cervical High-Grade Squamous Intraepithelial Lesions (NCT02481414), a randomized phase 2 study. The primary outcome is Number of Subjects With Complete Response With the Intention-to-treat (ITT) Analysis.

2. Clinical Question

3. Trial Design

This is a Phase II, randomized, parallel-arm clinical trial with two biological interventions: PepCan and Candin. The registry describes the trial as double-blinded in its official title and records quadruple masking in its design information. Eligible participants were to be randomized to the two arms at a 1:1 ratio. The registry records an enrollment of 81 participants. The primary outcome counts were reported for 39 participants in the PepCan arm and 42 in the Candin arm.

Both groups were assigned four injections, with three weeks between injections. The study description places clinical and virological response assessments at 6 and 12 months. It describes immunological assessments at four time points: before vaccination, after two injections, 6 months after four injections and 12 months after four vaccinations. Safety was to be assessed from enrollment to the 12 Month Visit. The primary endpoint, however, is recorded at 15 months from the time of the last vaccination; that is the outcome timeframe to use when interpreting the posted primary counts.

The trial is marked completed. Its recorded start date is 2015-11-30, and its primary completion date is 2022-09-14. The registry lists one secondary outcome, safety assessed by injection-related adverse events. The number of outcome measures is recorded as 5, while no analysis results are listed in the registry record. More detailed information about the randomization procedure, concealment, masking procedures, adherence, or the trial’s original statistical plan is not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: ITT (subjects who were eligible and randomized)

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 Subjects With Complete Response With the Intention-to-treat (ITT) Analysis, measured over 15 months from time of last vaccination.

The primary endpoint is a participant count: the number with a complete histological response in the intention-to-treat analysis. Complete response is defined as histological regression of moderate or severe cervical dysplasia to absence of cervical dysplasia, assessed using biopsies under a stringent definition. This is a binary outcome at the participant level: each eligible, randomized participant either meets the stated response definition or does not.

A biopsy-based endpoint gives the outcome a specific histological basis, rather than relying only on a symptom report or a virological measure. The registry’s definition makes the threshold for response explicit: the biopsy must indicate absence of cervical dysplasia after the starting condition of moderate or severe dysplasia. The endpoint is recorded for 15 months from the time of the last vaccination. It should therefore be distinguished from the study description’s clinical and virological assessments at 6 and 12 months, and from its immunological assessments at specified time points.

The intention-to-treat population is defined as eligible participants who were randomized. Using that population connects the comparison to randomized assignment, even if participants’ subsequent treatment exposure or follow-up status differed; how such issues were handled is not reported in the registry record. The endpoint measures histological response, not every possible clinical, virological, immunological or safety outcome. It also does not identify the cause of a response in an individual participant.

7. Results Posted in the Registry

• Candin: 47.6% (20/42) versus 30.8% (12/39) on control; risk difference 16.8 percentage points (95% CI -4.1 to 37.8), risk ratio 1.55 (0.88–2.73); unadjusted two-proportion z-test p = 0.121.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a count of participants meeting a binary response definition. In general, a binary outcome records whether each participant has the event of interest or does not. Here, the event is complete histological response as defined by the registry. Counts and denominators show both how many participants met that definition and the size of each arm contributing to the posted result.

What does a risk difference express?

In general, a risk difference subtracts the event proportion in one group from the event proportion in the other. It expresses an absolute contrast on the event-probability scale. The posted estimate is 0.169, with Candin compared against PepCan. A positive estimate in this orientation means the observed response proportion was higher in Candin; the estimate alone does not establish whether the underlying difference is distinguishable from zero. The interval, which extends from -0.041 to 0.378, communicates uncertainty around that estimate.

How do risk and odds ratios differ?

In general, a risk ratio compares event proportions directly, whereas an odds ratio compares the odds of an event. They are relative measures and can be less immediately intuitive than a risk difference. The posted risk ratio is 1.548, with an interval from 0.877 to 2.73; the posted odds ratio is 2.045, with an interval from 0.823 to 5.084. For each ratio, a value corresponding to no relative difference is 1. Both posted intervals include that value. Ratios and absolute differences describe the same comparison using different scales, so the interpretation should remain tied to the endpoint, the arm ordering and the uncertainty.

What does a confidence interval communicate?

In general, a confidence interval is a range of estimates compatible with the observed data under a specified statistical procedure. It shows the precision of an estimate: a narrower interval indicates less sampling uncertainty than a wider interval on the same scale. An interval that includes the no-difference value does not prove there is no effect. It indicates that the data and method do not exclude that value at the interval’s confidence level. The confidence level and the interval-construction method are not reported in the registry record, so they should not be inferred from the displayed limits.

What does the p-value add?

The unadjusted p-value is 0.121. In general, a p-value describes the compatibility of observed data with a specified null model, given the assumptions of the test. It is not the probability that the null model is true, and it does not measure the probability that the result happened “by chance.” A p-value also does not convey the size of an effect or its precision, which is why the estimate and interval matter. The test used to obtain this p-value is not reported in the registry record. The label unadjusted indicates that the posted value is not presented as adjusted for multiple comparisons.

Why does over-dispersion matter in general?

For count outcomes, over-dispersion means that the observed variability is greater than a statistical model expects. If it is ignored, standard errors can be too small and intervals or tests can overstate precision. This trial’s primary endpoint is a participant count arising from a binary response, not a repeated-event count. The registry record does not report an over-dispersion assessment or a model-based analysis for this endpoint. The concept is relevant as a general statistical issue, but there is no basis in the record to say that over-dispersion was present or affected the result.

The counts and comparison statistics should be interpreted in the setting of random allocation and the stated intention-to-treat population. The registry describes randomization at a 1:1 ratio, but details of sequence generation and allocation concealment are not reported in the registry record. A statistical comparison cannot remove uncertainty arising from limited information, incomplete follow-up, measurement decisions or differences in how the outcome is assessed. The record does not describe these aspects in enough detail to assess their impact.

The trial is labeled quadruple masked, while its official title calls it double-blinded. Those are the registry’s descriptions; specific masking roles and procedures are not reported in the registry record. Masking can, in general, help limit differences in care, measurement or outcome assessment that might influence a comparison. Whether it was maintained in practice is not addressed in the posted results.

10. Confidence Intervals and Precision

The primary estimate is a risk difference of 0.169. Its interval extends from -0.041 to 0.378, covering values on both sides of zero. In general, an interval around an effect estimate represents uncertainty due to sampling and the statistical method. The breadth of the posted interval indicates that the magnitude of the arm difference is not estimated with high precision. The interval includes a value of no absolute difference, but also allows for differences in either direction within its limits.

The relative measures tell a similar precision story. The risk ratio is 1.548, with an interval from 0.877 to 2.73; the odds ratio is 2.045, with an interval from 0.823 to 5.084. Each interval includes the value corresponding to no relative difference. Both also span materially different possible relative effects, so neither provides a narrowly defined estimate. These measures use different scales and should not be compared by their numerical size alone.

The registry record does not report the confidence level or the method used to construct these intervals. They should therefore be read as the posted uncertainty intervals, without assuming a particular confidence level or calculation procedure. The unadjusted p-value of 0.121 is another summary of the comparison, but it does not replace the interval’s information about the range of estimates consistent with the data.

The arm counts are 39 and 42, and the primary event counts are 12 and 20. With a binary endpoint, the amount of information depends on both the number of participants and how frequently the event is observed. These counts give context for why substantial uncertainty can remain. Precision is about how tightly the data estimate an effect, not whether a result is important or whether a treatment should be used.

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, not total participants across both arms and not total events. They are illustrations calculated from the observed effect, not the trial’s original design calculation. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

The rows consider planning for 100%, 75% and 50% of the observed effect. The 100% row uses the full observed effect as the planning target; the other rows use progressively smaller effects. For each target, the 80% power column gives the participants per arm under these assumptions for an 80% chance of detecting an effect of that size if it is present. The 90% power column gives the corresponding planning number for a 90% chance. These are design concepts: power is calculated before a study, under a specified effect and model, and does not tell whether a particular observed result is true.

Smaller effects require more participants to detect under the same assumptions, which is why the planning requirements increase as the target effect becomes a smaller fraction of the observed effect. The reported figures are based on this trial’s observed effect, so they should not be treated as a definitive recommendation for a future study. A future design would need its own justified target effect and assumptions. This is not observed power; it is a planning illustration. The registry record does not report the assumptions used for the trial’s original sample-size justification.

The same interpretation applies to any curve accompanying these planning values: it relates assumed effect size and planned sample size under the stated model, not the probability that the posted result is correct. The figures are sensitive to the planning assumptions and should not be read as a summary of the trial’s achieved 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 = 0.308; treatment proportion p₁ = 0.476; average p̄ = 0.392.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6904 = 1.3532.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6800 = 0.5723.
4. n = (1.3532 + 0.5723)² / (0.1685)² = 130.6, rounded up to 131 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 <- 0.307692307692308                          # control proportion
p1 <- 0.476190476190476                          # 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(2481414)
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 = 131 (80% power), 175 (90% power)
 75% of observed effect: n per arm = 229 (80% power), 305 (90% power)
 50% of observed effect: n per arm = 502 (80% power), 672 (90% power)
power.prop.test: 130.6 
Simulated power at n = 131 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. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome measure and one secondary outcome, safety assessed by injection-related adverse events. It also records 5 outcome measures in total. The available record does not give a complete account of all outcome definitions, their planned hierarchy, or the statistical procedures attached to them. It lists 0 analyses. A multiplicity strategy, such as a prespecified adjustment or a hierarchy controlling how outcomes are tested, is not reported in the registry record.

The posted primary p-value is explicitly unadjusted. When several outcomes, time points or comparisons are examined, the chance of at least one apparently unusual result can increase. In general, multiplicity methods address that issue by defining how evidence across tests will be interpreted. The record describes several assessment types and time points, but does not state how these were handled analytically. It is therefore not possible to determine from the registry record whether, or how, multiplicity was addressed. The unadjusted p-value should not be assumed to account for other outcomes or analyses.

The primary analysis population is described as eligible and randomized participants under an intention-to-treat approach. The arm-level primary counts are reported for 39 PepCan participants and 42 Candin participants. The registry does not explain whether all randomized participants had an assessable biopsy, how missing endpoint assessments were treated, or whether any participants were excluded from the analysis after randomization. Missing-data methods, imputation procedures and sensitivity analyses are not reported in the registry record.

The record also does not describe a per-protocol analysis, subgroup analyses, covariate adjustment or interim analyses. These should not be assumed to have occurred, nor should their absence from the record be treated as proof that they did not occur outside the posted information. The available results support interpretation of the stated counts and unadjusted comparison, while leaving important details about analysis planning and missingness unresolved.

14. 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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: headache (2.6%), fetal death (2.6%), psychiatric disorders - other specify (2.6%), appendicitis (2.4%).

The serious adverse event figures count participants with at least one serious adverse event in each arm: 3 of 39 in PepCan and 2 of 42 in Candin. The posted death counts are 0 in each arm. The registry also reports participants with other, non-serious adverse events: 37 of 39 in PepCan and 40 of 42 in Candin. These are separate serious and other adverse-event summaries; they should not be added together because the record does not establish whether the same participant could appear in both categories.

The listed serious adverse event terms and percentages are Headache, 2.6%; Fetal Death, 2.6%; Psychiatric Disorders - Other Specify, 2.6%; and Appendicitis, 2.4%. The registry record does not specify in this listing whether these terms represent unique participants, events or another reporting unit, or whether each event was judged related to treatment. The listed percentages should therefore be read as reported rather than converted into participant counts or interpreted as evidence of causation.

These figures describe the posted safety data and do not, by themselves, establish comparative safety. The record’s secondary outcome is safety assessed by injection-related adverse events, but the detail available does not explain the definitions, collection procedures, seriousness criteria or attribution process used for these summaries.

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

The posted result describes a randomized comparison of PepCan and Candin on a stringent biopsy-defined complete-response outcome. The observed counts were 12 of 39 in the PepCan arm and 20 of 42 in the Candin arm. The reported risk difference is 0.169, with an interval from -0.041 to 0.378, and the unadjusted p-value is 0.121. These statistics describe the direction and uncertainty of the observed comparison; they do not establish a definitive treatment effect.

The interval includes zero, and the relative-measure intervals include the values corresponding to no difference. At the same time, the intervals extend across a range of possible effects. Thus, the result is not a precise estimate of the size of an underlying difference. The p-value should not be interpreted as the probability that the null hypothesis is true, and it does not say how likely a particular effect is to be clinically important.

The endpoint is specifically histological regression to absence of cervical dysplasia as assessed by biopsy. It is not a summary of all clinical, virological, immunological or safety outcomes recorded or described for the trial. The primary timeframe is 15 months from the time of the last vaccination. Findings at other assessment times, or for other endpoints, cannot be inferred from this primary result.

The safety summaries report serious and other adverse-event counts and the listed serious event terms. They do not show whether an event was caused by an intervention, and they do not replace a fuller safety analysis. Likewise, the planning illustrations do not describe the study’s observed power or prove that a future trial would require the listed sample sizes. Their meaning depends on their stated design assumptions and target effect.

Important analytical details—including missing-data handling, the method for the primary comparison, multiplicity procedures and the original sample-size justification—are not reported in the registry record. The most defensible reading is therefore descriptive and appropriately cautious: the posted counts favor a higher response proportion in Candin, but the uncertainty intervals include no difference and do not tightly determine the magnitude of any underlying contrast.

16. Why This Trial Matters Statistically

This trial illustrates why an effect estimate, its uncertainty and the underlying event counts should be read together. A single p-value cannot communicate the direction or possible magnitude of a difference, while a point estimate alone can create a false impression of certainty. Here, the reported risk difference is positive in the Candin-versus-PepCan orientation, but its interval includes zero and is broad. The arm counts provide essential context for that uncertainty.

The endpoint definition also matters. “Complete response” is not left as a general label: the registry specifies biopsy-assessed regression of moderate or severe dysplasia to absence of dysplasia. A stringent, explicitly defined endpoint makes clear what was counted, while also limiting the scope of interpretation to that particular histological outcome and timeframe.

The trial’s design makes a randomized arm comparison possible, but the result is only as interpretable as the reporting allows. The record identifies an intention-to-treat population and the arm denominators, yet omits key details about missing data, analysis methods, multiplicity and the original sample-size justification. These omissions do not change the posted counts, but they constrain how fully readers can assess the statistical analysis.

Finally, planning calculations based on an observed effect are not a substitute for a prospectively justified target effect. They are useful for illustrating how planned sample size changes as assumptions about the effect change. Distinguishing such planning illustrations from trial results helps prevent a retrospective calculation from being mistaken for evidence about the strength or reliability of the observed finding.

17. 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 leaves several trial-specific questions unresolved. It does not report the full eligibility criteria, the random sequence-generation procedure, allocation concealment or the practical roles covered by quadruple masking. The official title describes the study as double-blinded, but the record does not explain how that label relates to its quadruple-masking designation or whether masking was maintained.

The primary outcome is recorded at 15 months from the time of the last vaccination, while the study description also identifies clinical and virological assessments at 6 and 12 months. The record does not provide a detailed schedule linking all assessments to the endpoint or explain how timing differences were handled. The endpoint is based on biopsy, but biopsy procedures, pathology review, assessor masking and adjudication are not reported in the registry record.

Although the primary population is defined as eligible and randomized, the registry does not describe missing biopsies, loss to follow-up, exclusions after randomization, adherence to injections or treatment discontinuation. It does not state how missing endpoint values were handled or report sensitivity analyses. The method used for the unadjusted comparison and for its intervals is also not reported. A multiplicity plan, interim analyses and the original sample-size justification are not reported in the registry record.

The safety information is limited to posted participant counts and a short list of serious adverse event terms. Definitions, treatment attribution and the reporting unit for the listed percentages are not explained. These gaps restrict assessment of both the statistical analysis and the context of the safety summaries; they do not justify assuming that any unreported procedure was or was not undertaken.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Clinical Trial of PepCan to Two Therapy Arms for Treating Cervical High-Grade Squamous Intraepithelial Lesions — NCT02481414.
• Registry record last updated 2023-12-18; status last verified 2023-11.
• Results first posted 2023-12-18.
• 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.

21. Record Summary

NCT02481414 is a completed, randomized Phase II parallel-arm trial sponsored by the University of Arkansas. It compared four injections of PepCan with four injections of Candin, with three weeks between injections. The registry records enrollment of 81 and describes masking as quadruple; the official title calls the trial double-blinded.

The primary outcome was the number of eligible, randomized participants with complete histological response, defined as regression of moderate or severe cervical dysplasia to absence of dysplasia by biopsy. The timeframe was 15 months from the last vaccination. The posted counts were 12 of 39 for PepCan and 20 of 42 for Candin. The risk difference was 0.169, with an interval from -0.041 to 0.378, and the unadjusted p-value was 0.121.

The record lists safety as a secondary outcome and reports serious and other adverse-event counts. It does not report the original sample-size assumptions, detailed analysis methods or missing-data procedures.