Efficacy, Immunogenicity, and Safety Study of V503 (9-valent Human Papillomavirus [9vHPV] Vaccine) in Japanese Males (V503-064): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy, Immunogenicity, and Safety Study of V503 (9-valent Human Papillomavirus [9vHPV] Vaccine) in Japanese Males (V503-064) (NCT04635423), a randomized phase 3 study. The primary outcome is Base Study: Combined Incidence of Human Papillomavirus (HPV) 6/11/16/18-related Anogenital Persistent Infection.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, placebo-controlled, parallel-group study in Japanese males aged 16 to 26 years. The registry lists triple masking. Its stated purposes were to evaluate efficacy against HPV-related anogenital persistent infection and to assess safety and tolerability. The study had a base study and an extension study. The base study compared V503 with placebo; extension arrangements offered vaccination to some participants according to their original assignment and whether they had completed the vaccine series.

The registry reports enrollment of 1059 and a completed study. It records the start as 2020-11-30 and primary completion as 2023-12-31. These are registry dates, not a description of the duration each participant was followed. The primary endpoint timeframe is up to approximately 36 Months. The registry also lists immunogenicity outcomes, including geometric mean titers and seroconversion, with analyses described for all randomized participants and for heterosexual male and male who have sex with males subgroups.

The primary efficacy endpoint was analyzed in a per-protocol efficacy population with specified HPV-type eligibility and data requirements, rather than simply counting every randomized participant. The record describes vaccination, post-dose sample collection, and baseline serological and PCR status as part of eligibility. The remaining text of the population definition is incomplete in the registry record. The registry lists the primary incidence outcome and one additional incidence outcome for HPV 31/33/45/52/58-related infection. It also lists immunogenicity outcomes. The original design’s sample-size justification, the full protocol analysis plan, and the rationale for the selected enrollment are not reported in the registry record.

4. Participant Flow and Accounting

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

Base Study

Reasons for not completing this period:

Extension Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: HPV type 6/11/16/18 eligible participants with data available in PPE population within acceptable day ranges; received all 3 vaccinations of correct dose within 1 year, Month 7 swab samples collected postdose 3 with PCR result, seronegative to the appropriate HPV type at baseline and PCR-negative to appropriate HPV type on all samples collected from baseline through Month 7, and no protocol deviations that could interfere with the evaluation of participant's immune response to V503.

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 Base Study: Combined Incidence of Human Papillomavirus (HPV) 6/11/16/18-related Anogenital Persistent Infection, measured over Up to approximately 36 Months.

The primary endpoint is the incidence of combined HPV 6/11/16/18-related anogenital persistent infection, expressed as cases per 100 person-years of follow-up. The registry defines a case using either repeated evidence of infection or specified HPV-associated pathology. The infection criterion requires PCR positivity for at least one applicable HPV type in samples from consecutive visits, with the visits separated by at least the stated interval. The pathology route covers a diagnosis of condyloma, specified intraepithelial neoplasia, or cancer in the listed anogenital sites, together with PCR detection of an applicable HPV type in tissue and evidence of the same type at a separate adjacent visit.

Using person-time places the number of cases in relation to the follow-up time contributed by eligible participants. In general, this is useful when individuals contribute different amounts of observation time or when an outcome is recorded as an event rate. It is not the same quantity as the proportion of participants who ever had an event. The registry specifies that the primary analysis uses applicable HPV-type-eligible participants with available data in the per-protocol efficacy population and reports cases per 100 person-years.

The endpoint addresses persistent infection rather than a single positive test. Requiring persistence or pathology with supporting HPV evidence is intended to distinguish the defined endpoint from a one-time detection. The registry’s definition is specific to the eligible HPV types and the per-protocol population. It does not establish that every HPV-related condition, every infection, or every clinical outcome is captured by this endpoint.

7. Results Posted in the Registry

• V503: 0.20 versus 2.20 (Cases per 100 Person-years) on control; rate ratio 0.09 (95% CI 0.03–0.30, approximate, Poisson model); 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.

Base Study: Combined Incidence of HPV 31/33/45/52/58-related Anogenital Persistent Infection

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • V503: 0.70 versus 1.90 (cases per 100 Person-years) on control; rate ratio 0.37 (95% CI 0.18–0.75, approximate, Poisson model); p ≈ 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically lower for V503 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry’s secondary results follow a broadly consistent direction with the primary incidence finding: the posted secondary incidence comparison favors V503, and the immunogenicity outcomes assess vaccine responses across the listed HPV types and participant groups. These endpoints address related but distinct questions. Incidence of persistent infection is a clinical virologic outcome; geometric mean titers and seroconversion describe immune response. Agreement in direction across related measures can add context, but it does not make the measures interchangeable or establish effects on outcomes that were not assessed.

Secondary analyses generally carry less inferential weight than a designated primary endpoint, especially when several outcomes, HPV types, or subgroups are examined. Multiple testing can increase the chance that at least one result appears noteworthy even when no corresponding effect exists. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting the secondary outcomes. Their reported p-values should therefore be treated as unadjusted evidence, not as definitive confirmation on their own.

Subgroup immunogenicity results also answer narrower questions than the overall randomized comparison. Subgroup patterns can be informative, but separate subgroup results do not necessarily establish that responses differ between subgroups; that requires an appropriate comparison of the difference in effects. Such an interaction analysis is not reported in the registry record. The secondary findings are best read as supportive context around the primary result, with attention to endpoint definitions, analysis populations, precision, and the unreported multiplicity plan.

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

• Base Study: Combined Incidence of HPV 31/33/45/52/58-related Anogenital Persistent Infection
• Base Study: Geometric Mean Titers (GMTs) to HPV 6/11/16/18/31/33/45/52/58 - All Randomized Participants
• Base Study: Geometric Mean Titers (GMTs) to HPV 6/11/16/18/31/33/45/52/58 - Heterosexual Males (HM) Participant Subgroup
• Base Study: Geometric Mean Titers (GMTs) to HPV 6/11/16/18/31/33/45/52/58 - Males Who Have Sex With Males (MSM) Participant Subgroup
• Base Study: Percentage of Participants With Seroconversion to HPV 6/11/16/18/31/33/45/52/58 - All Randomized Participants
• Base Study: Percentage of Participants With Seroconversion to HPV 6/11/16/18/31/33/45/52/58 - Heterosexual Males (HM) Participant Subgroup
• Base Study: Percentage of Participants With Seroconversion to HPV 6/11/16/18/31/33/45/52/58 - Males Who Have Sex With Males (MSM) Participant Subgroup

9. Statistical Interpretation

10. Statistical Methods Explained

What does an incidence rate represent?

The registry reports cases per 100 person-years. In general, a person-time rate relates event counts to the time participants were observed and at risk under the analysis definition. Person-time is useful when follow-up differs across participants, because it accounts for the amount of observation contributing to the rate. The rate is not a direct statement of the percentage of participants who experienced the endpoint. Nor does it, by itself, tell how many cases would occur in a different population or under a different follow-up schedule.

The recorded endpoint is a combined incidence measure. It uses the registry’s stated criteria for persistent PCR-positive infection or qualifying pathology with HPV evidence. The analysis population is per protocol and restricted to participants eligible for the applicable HPV types and with data available under the recorded requirements. These choices define what the rate means. They also mean the result should not be generalized automatically to all randomized participants or to people who do not meet those conditions.

How should a rate ratio be read?

In general, a rate ratio compares the incidence rate in one group with the rate in another. A ratio of one represents equal rates; values below one indicate a lower rate in the numerator group, and values above one indicate a higher rate. The recalculated primary rate ratio is 0.091 for V503 relative to placebo. Its confidence interval is 0.028 to 0.298. This is an unadjusted recalculation from the posted summary rates, not a replacement for the sponsor’s reported analysis.

When an outcome is modeled as a count of events over exposure time, a Poisson approach is one general method for estimating a rate comparison. Such a model commonly treats event counts as having a variance related to the mean under its assumptions. If the data vary more than that model allows, a condition often called over-dispersion, standard errors can be too small and confidence intervals too narrow unless the analysis accounts for it. The registry does not report a dispersion estimate for this endpoint, and the posted rate comparison is identified as Poisson. No conclusion about whether over-dispersion was assessed can be drawn from the registry record.

Why are the sponsor’s and recalculated estimates different in form?

The sponsor reports observed efficacy using the Exact Binomial Method Chan and Bohidar, together with a 95% confidence interval and p-value. The simple recalculation instead uses posted incidence rates to obtain a rate ratio and a Poisson comparison. An efficacy estimate and a rate ratio are related ways to express a relative contrast, but the methods, estimands, and interval calculations need not be identical. The registry does not describe the full derivation of the sponsor’s analysis beyond its named method and reported summary. The discrepancy flag is false; the record does not identify a discrepancy between the posted values.

The sponsor’s reported primary efficacy estimate is 89.3, with a 95% confidence interval from 55.4 to 98.2 and p < 0.001. The rate-ratio recalculation is an additional unadjusted statistical reading of the posted arm rates. It should not be interpreted as a second independent study or as a correction to the sponsor’s analysis.

What does the p-value answer?

In general, a p-value describes how compatible the observed data are with a specified null model, assuming that model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The sponsor reports p < 0.001 for the primary efficacy analysis. The recalculated primary comparison also reports p < 0.001. Those values indicate statistical evidence against the null comparison under the respective analyses, but they do not remove uncertainty about the magnitude or applicability of the result.

The registry’s secondary incidence analysis reports p = 0.023. Secondary results require more caution because testing multiple outcomes can increase the chance of at least one apparently notable result. The record does not report a multiplicity adjustment. A p-value should therefore be considered alongside the endpoint’s status, the estimate, its interval, the population, and the broader set of analyses rather than treated as a stand-alone verdict.

How do the populations affect interpretation?

The trial was randomized, but the primary endpoint’s stated analysis population is per protocol. A per-protocol analysis focuses on participants meeting the listed requirements, including correct vaccination and available endpoint data. It can answer a focused question about outcomes among those meeting those criteria. It may not preserve all the advantages of comparing every randomized participant if entry into the analysis depends on events after randomization or on data availability. The registry’s complete population criteria and details of missing-data handling are not reported in the registry record.

The posted arm counts for the primary comparison are the numbers identified with the analysis, while the registry separately reports overall enrollment and safety populations. These quantities refer to different analysis contexts and should not be substituted for one another. The primary result should be read as applying to the specified per-protocol efficacy population and endpoint, not as a complete summary of all outcomes among all randomized participants.

11. Confidence Intervals and Precision

The sponsor’s primary efficacy estimate is 89.3, with a 95% confidence interval from 55.4 to 98.2. In general, a confidence interval gives a range of values compatible with the data and the method used, while reflecting sampling uncertainty under that method’s assumptions. It is not a guarantee that the true value lies in the interval, nor does it account automatically for biases, missing data, or limitations in endpoint measurement. The interval’s width signals that the exact size of the efficacy estimate remains uncertain.

The recalculated rate ratio is 0.091, with a confidence interval from 0.028 to 0.298. Because this is a different estimate and method from the sponsor’s efficacy analysis, its interval should be interpreted on the rate-ratio scale rather than read as if it were the sponsor’s interval. The limits indicate uncertainty around the relative rate comparison, while the entire interval remains below one. This is consistent with a lower observed rate in the V503 group under the recalculated comparison.

For the secondary incidence endpoint, the sponsor reports observed efficacy of 63.5, with a 95% confidence interval from 2.7 to 86.0. Its breadth indicates substantial uncertainty about the magnitude of that secondary estimate. Confidence intervals address sampling variability under a specified analysis; they do not resolve questions about multiplicity, completeness of follow-up, generalizability, or whether a result will be replicated. The registry does not report all details needed to assess those issues fully.

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 values are participants per arm, not total event counts. The registry’s planning illustration assumes a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. It uses the observed effect as its reference and considers planning for 100%, 75%, or 50% of that observed effect. These assumptions describe the illustration, not the trial’s original design. The original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a future study to have an 80% chance of detecting the stated effect under those assumptions, if that effect and the model assumptions hold. The 90% power column gives the corresponding planning number for a 90% chance. These are prospective planning probabilities under a hypothetical design, not probabilities that the observed finding is true.

The illustration shows that planning for a smaller effect requires more participants per arm. This is expected in general: smaller differences are harder to distinguish from random variation, so a design generally needs more information to detect them at a chosen significance level and power. The counts are not observed enrollment requirements, and they should not be treated as a reconstruction of the actual trial’s design. This is not observed power.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 0.0220; treatment rate λ₁ = 0.0020 events per patient-year; follow-up T = 3.00 years.
2. n = (1.96 + 0.842)² × (1/0.0220 + 1/0.0020) / (3.00 × [ln(0.091)]²) = 248.2, rounded up to 249 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
lambda0 <- 0.022                      # control rate, events per patient-year
lambda1 <- 0.002                      # treatment rate
tt      <- 3                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(4635423)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 249 (80% power), 333 (90% power)
 75% of observed effect: n per arm = 259 (80% power), 347 (90% power)
 50% of observed effect: n per arm = 358 (80% power), 479 (90% power)
Simulated power, Poisson counts, n = 249 per arm: 0.960
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.728

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The registry’s sponsor-reported primary analysis uses the Exact Binomial Method Chan and Bohidar and reports observed efficacy of 89.3, a 95% confidence interval from 55.4 to 98.2, and p < 0.001. The posted arm rates also permit a simple unadjusted recalculation, which expresses the comparison as a rate ratio of 0.091 with a confidence interval from 0.028 to 0.298 and p < 0.001. These estimates use different statistical expressions and methods, so their values and intervals should not be compared as though they were outputs of the same procedure.

The recalculation is a supplementary reading of the posted summary statistics; it does not replace the sponsor’s analysis. The discrepancy flag is false, and the registry record does not indicate a conflict between the reported results and the recalculation. The sponsor’s analysis is the primary reported efficacy result, while the recalculation helps express the arm-rate contrast on a ratio scale. Neither analysis changes the endpoint definition or the limits of the per-protocol population.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when an analysis examines several outcomes, comparisons, HPV types, or subgroups. In general, the more statistical tests considered, the greater the chance that at least one will meet a conventional significance threshold by chance alone. A prespecified hierarchy or adjustment can help control that risk, but the registry record does not report whether such a plan was used for the secondary outcomes. The reported secondary p-values should therefore be interpreted cautiously and are not equivalent to a single confirmatory primary test.

The registry identifies a primary endpoint and lists additional incidence and immunogenicity outcomes, including subgroup outcomes. It does not report a complete statistical analysis plan, the testing hierarchy, or a multiplicity procedure. It is also not reported in the registry record whether interim analyses were conducted. The absence of these details from the registry record does not establish that a procedure was absent; it limits what can be verified from the record.

Missing-data handling is another uncertainty. The primary endpoint description specifies participants with available data in the per-protocol efficacy population and includes requirements involving vaccination and sample collection. The registry record’s text describing the full primary analysis population is incomplete. It does not report how missing samples, incomplete follow-up, protocol deviations, or other unavailable outcome data were handled, nor does it give a sensitivity analysis for missing data. These omissions matter because analysis eligibility and data availability can affect the population represented by the reported rate.

The study’s randomized design is relevant to the base-study comparison, but the primary per-protocol analysis is not automatically equivalent to an analysis of all randomized participants. The registry does not report enough detail to assess fully how the analysis population was determined or how missingness might influence the estimate. Accordingly, conclusions should remain tied to the posted per-protocol result, with uncertainty about unreported analysis and missing-data procedures kept explicit.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: gastroenteritis viral (0.3%), ankle fracture (0.3%), colitis ulcerative (0.2%), appendicitis (0.2%), covid-19 (0.2%).

The base-study safety record lists serious adverse events in the V503 group among 529 participants at risk and in the placebo group among 530 participants at risk. The affected counts are 7 and 5, respectively. The record reports zero deaths in each of those base-study groups. These are descriptive counts; by themselves they do not establish that an event was caused by the assigned injection or indicate whether the groups differ statistically.

The registry also reports extension safety groups. In the V503-to-extension group, 2 were at risk for serious adverse events and none were affected; in the placebo-to-extension group, 381 were at risk and 2 were affected. These extension groups reflect the subsequent vaccination arrangements and should not be conflated with the randomized base-study comparison. The record’s leading serious-event terms include gastroenteritis viral, ankle fracture, colitis ulcerative, appendicitis, COVID-19, and Campylobacter gastroenteritis, each with its posted percentage. Serious adverse event counts are not the same as counts of all adverse events, and the posted figures alone do not establish causation or comparative risk.

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

The posted primary result shows a lower observed incidence rate of the defined HPV 6/11/16/18-related persistent infection endpoint in the V503 group than in the placebo group within the per-protocol efficacy population. The sponsor’s reported efficacy estimate and the unadjusted rate-ratio recalculation both indicate a comparison favoring V503 for this endpoint. Their confidence intervals communicate uncertainty about the magnitude, and the result is specific to the registry’s case definition, eligible HPV types, follow-up, and analysis population.

The finding does not by itself establish effects on every HPV type, every HPV-associated condition, or outcomes beyond the recorded endpoint and follow-up. It is not a direct estimate of the proportion of all randomized participants who would experience disease, because the primary measure is an incidence rate per person-time and the primary population is per protocol. It does not show that each participant had the same outcome or that an observed event was caused by an intervention.

The secondary incidence and immunogenicity results add context but do not erase the limitations of multiple outcomes or unreported analysis details. The registry does not report the complete original statistical plan, the full primary population definition, or missing-data procedures. Nor does the study record alone establish how results apply to populations outside the stated Japanese male age range or to settings not represented by the study. These are boundaries on interpretation, not claims that the results are invalid.

18. Why This Trial Matters Statistically

This study illustrates why an endpoint’s statistical form matters. The primary result is a rate per person-time, not a simple percentage of participants with an event. Its interpretation depends on the event definition, follow-up, and the population contributing data. Reading the endpoint and analysis population alongside the estimate avoids treating a rate as though it were a risk proportion or assuming that every enrolled participant contributed to the primary analysis.

It also shows the value of keeping sponsor-reported analyses distinct from transparent recalculations of posted summary statistics. The sponsor reports an efficacy measure using a named exact method; a Poisson recalculation expresses the posted incidence rates as a rate ratio. Those summaries provide related perspectives, but they are not interchangeable. Reporting the method and scale makes it easier to understand what each estimate represents.

Finally, confidence intervals, secondary outcomes, and planning illustrations answer different questions. Intervals describe precision under an analysis, secondary findings require attention to multiplicity, and planning values describe hypothetical future designs rather than the strength of evidence observed in the completed study. The distinction is especially important when the registry record leaves the original design assumptions, missing-data approach, and full analysis plan unreported. These statistical features help readers assess the evidence without extending it beyond the defined endpoint and population.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The primary endpoint analysis is described for a per-protocol efficacy population, with eligibility requirements involving vaccination, sample collection, and baseline status. The registry’s population description is incomplete, so the full set of criteria cannot be assessed from the record. The primary result therefore should not be assumed to represent all randomized participants.

The record does not report the original sample-size justification, full statistical analysis plan, missing-data methods, sensitivity analyses, or whether interim analyses were conducted. It also does not report a multiplicity adjustment for the listed secondary outcomes. These gaps limit assessment of the design rationale, robustness to missing observations, and confirmatory status of secondary findings. The planning illustration is based on the observed effect and is not a substitute for the trial’s original design calculation.

The primary outcome combines specified HPV types and infection or pathology criteria. It does not cover every HPV type or every possible HPV-related clinical outcome. The registry reports follow-up up to approximately 36 Months, so the findings do not describe outcomes outside that recorded timeframe. The extension’s vaccination arrangements also mean its groups should not be treated as a continuation of the original placebo-controlled comparison for the base-study endpoint. Finally, serious adverse event counts are descriptive and do not, without further analysis and context, establish causation or a comparative safety effect.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy, Immunogenicity, and Safety Study of V503 (9-valent Human Papillomavirus [9vHPV] Vaccine) in Japanese Males (V503-064) — NCT04635423.
• Registry record last updated 2026-06-11; status last verified 2026-05.
• Results first posted 2025-01-13.
• 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

The registry describes a completed, phase 3, randomized, triple-masked, parallel-group placebo-controlled study of V503 in Japanese males aged 16 to 26 years. Enrollment was 1059. The base study compared three-dose V503 with placebo and assessed HPV-related persistent infection, immunogenicity, and safety; an extension offered vaccination to eligible participants.

For the primary per-protocol efficacy endpoint, the registry reports rates of 0.2 and 2.2 cases per 100 person-years for V503 and placebo. The sponsor reports observed efficacy of 89.3, with a 95% confidence interval from 55.4 to 98.2 and p < 0.001. Interpretation is specific to the endpoint definition and analysis population. Important details, including the complete original statistical plan and missing-data handling, are not reported in the registry record.