Evaluation of Immunogenicity and Safety of VARIVAX® Passage Extension 34 (PE34) Process in Children (V210-A03): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of Immunogenicity and Safety of VARIVAX® Passage Extension 34 (PE34) Process in Children (V210-A03) (NCT03239873), a randomized phase 3 study. The primary outcome is Percentage of Participants With Varicella Zoster Virus Antibody Levels ≥5 Glycoprotein Enzyme-linked Immunosorbent Assay (gpELISA) Units/mL.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, double-blind, multicenter, controlled study with a parallel-group model. The registry record lists triple masking. It enrolled 600 participants and is marked completed. The study began on 2017-10-17, with primary completion on 2018-08-14.

The two groups received different manufacturing-process versions of VARIVAX alongside M-M-R II. In both arm descriptions, the vaccines were given subcutaneously on Day 1 and Day 91, with VARIVAX in the left arm or thigh and M-M-R II in the right arm or thigh. Thus, the randomized comparison concerns PE34 versus the 2016 commercial process in the setting of concomitant M-M-R II, rather than a comparison of receiving versus not receiving the other vaccine.

The primary response-rate assessment was made 6 weeks (43 days) after vaccination 1. Its analysis population was participants who were seronegative at baseline and had postvaccination serology. The posted group estimates use 245 participants in the PE34 group and 239 in the 2016 commercial-process group for that endpoint. These analysis counts are not the same as the overall enrollment figure, because the primary endpoint has a defined seronegative population and requires postvaccination serology.

The study description names immunogenicity, safety, and tolerability as objectives. It also states hypotheses concerning non-inferiority of antibody response rate and mean antibody titer, and acceptability of the PE34 response rate. The registry record does not report the original sample-size justification, the full protocol, the identities of the masked parties, or the detailed allocation procedure.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis population included the number of participants with seronegative antibody titer (\<1.25 gpELISA units/mL) at baseline and postvaccination serology.

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 Percentage of Participants With Varicella Zoster Virus Antibody Levels ≥5 Glycoprotein Enzyme-linked Immunosorbent Assay (gpELISA) Units/mL, measured over 6 weeks (43 days) after vaccination 1.

The primary endpoint is the percentage of participants with VZV antibody titers at least 5 gpELISA units/mL, assessed 6 weeks (43 days) after the first vaccination. The endpoint definition restricts the response-rate calculation to participants whose baseline VZV titer was below 1.25 gpELISA units/mL. In other words, it measures the proportion of initially seronegative participants who reached the stated antibody threshold after vaccination.

An antibody response rate is a binary outcome at the participant level: each participant either meets the specified response definition or does not. Reporting the percentage makes the result interpretable as the share of the endpoint population meeting that definition. The confidence interval communicates uncertainty around that percentage, rather than showing the range of individual antibody titers.

The study description says that the primary hypotheses concerned both response rate and mean antibody titer, as well as whether the response rate was acceptable. The posted primary endpoint described in the registry record is the percentage meeting the antibody threshold; it does not itself report a mean titer. The registry record does not report the response-rate acceptability threshold or the non-inferiority margin. That absence matters when interpreting a non-inferiority test: the numerical test result cannot be fully evaluated without knowing the margin specified for the test.

The time point is an early postvaccination assessment, not a measure of how long the antibody response persists. The endpoint therefore answers a focused immunogenicity question at the stated follow-up time, rather than providing a measure of longer-term protection or clinical disease outcomes.

7. Results Posted in the Registry

• VARIVAX (2016 CP) + M-M-R II: 98.3% (235/239) versus 98.4% (241/245) on control; risk difference -0.0 percentage points (95% CI -2.3 to 2.2), risk ratio 1.00 (0.98–1.02); unadjusted two-proportion z-test p = 0.972.

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.

Percentage of Participants With Immunogenicity to Varicella Zoster Virus in Participants Initially Seropositive to Varicella Zoster Virus Antibody (≥ 5gpELISA Units/mL)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • VARIVAX (2016 CP) + M-M-R II: 97.5% (39/40) versus 100.0% (31/31) on control; risk difference -2.5 percentage points (95% CI -7.3 to 2.3), risk ratio 0.97 (0.93–1.02); unadjusted two-proportion z-test p = 0.375.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between VARIVAX (2016 CP) + M-M-R II and the control. The interval gives the range of effects that remain compatible with the data.

The registry's secondary outcome domains include additional immunogenicity assessments and safety and tolerability measures: fever, systemic symptoms and rash after each vaccination, injection-site reactions after each vaccination, adverse events, serious adverse events, and vaccine-related adverse events. These outcomes broaden the trial's scope beyond the primary antibody response rate, but they address different questions and may use different populations and follow-up periods.

The detailed secondary immunogenicity result reported for participants initially seropositive is high in both groups, but it concerns a distinct baseline population and has less precision than the primary analysis. It should be viewed as complementary descriptive evidence, not combined with the primary seronegative result. The primary endpoint remains the stated response-rate measure among participants who were seronegative at baseline.

The registry lists 18 posted secondary outcomes, 20 outcome measures, and 25 analyses. Those counts indicate that results may involve multiple endpoints and analyses; they do not establish that every result was prespecified or that every comparison has equal evidential weight. No single overall summary across the secondary outcomes is reported in the registry record. Consequently, the broad set of outcome names should not be taken as evidence that all results point in the same direction.

Unless an adjustment procedure is stated, secondary p-values are best treated as exploratory or descriptive rather than as stand-alone confirmatory evidence. With many outcomes, the chance of at least one apparently notable finding can increase simply because many comparisons are examined. The multiplicity adjustment, if any, is not reported in the registry record. The secondary outcomes can add context about immunogenicity and safety, but they do not replace the primary analysis or resolve the discrepancy between the sponsor analysis and the unadjusted recalculation.

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

• Percentage of Participants With Fever (≥102.2 °F Oral Equivalent)
• Percentage of Participants With Systemic Measles-like, Rubella-like, Varicella-like, Zoster-like Rash, and Mumps-like Symptoms After Vaccination 1 (Incidence > 0%)
• Percentage of Participants With Systemic Measles-like, Rubella-like, Varicella-like, Zoster-like Rash, and Mumps-like Symptoms After Vaccination 2 (Incidence > 0%)
• Percentage of Participants With Solicited Injection-site Erythema, Injection-site Swelling, or Injection-site Pain/Tenderness After Vaccination 1
• Percentage of Participants With Solicited Injection-site Erythema, Injection-site Swelling, and Injection-site Pain/Tenderness After Vaccination 2
• Percentage of Participants With One or More Adverse Events
• Percentage of Participants With One or More Serious Adverse Events
• Percentage of Participants With One or More Vaccine-Related Adverse Events

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: a participant either reaches the specified antibody threshold or does not. A percentage is the number meeting the response definition expressed relative to the endpoint population. This makes the result straightforward to describe, but it also means precision depends on both the observed response proportion and the number of participants contributing to the analysis.

What does a confidence interval describe?

A confidence interval gives a range of values reasonably compatible with the data under the method used. It is not a range containing a stated percentage of individual participants, nor does it mean that the true value has a probability equal to the confidence level of lying in that particular calculated interval. In repeated use of the same method under its assumptions, intervals at the stated confidence level would cover the underlying quantity at that rate.

Each arm's response percentage has its own interval. The comparison interval instead addresses the difference between the two groups. These answer related but distinct questions: an arm interval describes uncertainty in that group's response rate, while a difference interval describes uncertainty in the contrast. Looking only at whether the two arm intervals overlap is not a substitute for examining the interval and method for the between-group contrast.

How should the risk difference be read?

A risk difference subtracts one group's response proportion from the other's, with the sign depending on the order of subtraction. A value near zero indicates little observed separation in the proportions. Its confidence interval shows the range of differences compatible with the calculation. The unadjusted recalculation uses the posted summary proportions and does not account for any additional model, stratification, or protocol-specific procedure.

The sponsor reports a Miettinen and Nurminen risk-difference analysis and labels it a non-inferiority analysis. A non-inferiority test asks whether the data rule out a loss larger than a prespecified margin; it is not simply a test of whether the groups differ. A p-value from that test is meaningful relative to the margin and testing procedure. The margin is not reported in the registry record, and the sponsor's reported result is not the same calculation as the unadjusted recalculation.

Why distinguish the sponsor analysis from recalculation?

A recalculation from summary data can check whether simple arithmetic based on the posted group rates gives a similar contrast. It cannot recover details not contained in those summaries, such as the full analysis set, any stratification, missing-data rules, or adjustments used in the sponsor's analysis. Here the record explicitly flags a discrepancy, so the sponsor's own analysis takes precedence for the trial's reported non-inferiority conclusion. The recalculated estimate remains useful as a transparent, unadjusted description, but it should not be presented as the trial's prespecified inferential result.

The posted sponsor result reports a risk difference of 0.0, a confidence interval from -2.7 to 2.8, and p < 0.001. The recalculation reports -< 0.001, an interval from -0.023 to 0.022, and p = 0.972. The difference between these inferential results is a reason to keep method and purpose explicit, rather than choosing one p-value without context. The registry record does not report the full statistical analysis plan needed to reconcile the discrepancy.

What does the secondary seropositive analysis add?

The separately reported analysis among participants initially seropositive addresses a different population from the primary endpoint. Its percentages are 100.0% in the PE34 group and 97.5% in the 2016 commercial-process group, with 95% confidence intervals of 88.8% to 100.0% and 86.8% to 99.9%. The smaller analysis counts and broad intervals indicate less precision than in the primary analysis. Because baseline status differs, this result should not be combined with or treated as a replication of the primary seronegative analysis.

The primary estimate and the secondary estimate are proportions, not measurements of antibody concentration or clinical outcomes. The threshold turns a continuous titer into a response classification. That helps define a clinically interpretable immunogenicity endpoint, but information about how far above or below the threshold each participant's titer lies is not represented by the response percentage.

General statistical context: binary outcomes are often analyzed with methods designed for proportions and their differences. Different methods can yield slightly or materially different intervals and tests, especially when the analysis incorporates design features or uses a non-inferiority framework. The registry record names the sponsor's method for the reported risk difference, but it does not provide enough detail to reproduce the full analysis independently.

11. Confidence Intervals and Precision

For the primary endpoint, the PE34 group response estimate is 98.4%, with a 95% confidence interval from 95.9% to 99.6%. The 2016 commercial-process group estimate is 98.3%, with a 95% confidence interval from 95.8% to 99.5%. The intervals indicate that each estimated response rate is subject to sampling uncertainty, even though the point estimates are close to the upper end of the percentage scale.

Precision for the comparison is best assessed using the interval for the difference. The unadjusted recalculation gives a risk difference of -< 0.001, with a 95% confidence interval from -0.023 to 0.022. This range includes zero and allows for differences in either direction. It does not, by itself, establish non-inferiority; that conclusion depends on the sponsor's test and its margin. The sponsor reports a different non-inferiority analysis, and the record flags a discrepancy, so that sponsor analysis takes precedence.

The primary endpoint analysis includes 245 participants in the PE34 group and 239 in the 2016 commercial-process group. The secondary analysis among participants initially seropositive has smaller counts, 31 and 40, and broader arm-specific intervals. This illustrates a general point: fewer observations usually mean less precise estimates, though precision also depends on the observed proportions and analysis method.

Confidence intervals describe statistical uncertainty under the method; they do not account for every possible source of uncertainty. They do not resolve questions about endpoint selection, missing data, generalizability, or whether the antibody threshold predicts clinical outcomes. The registry record does not report enough detail to evaluate all such sources.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not a report of the trial's original design calculation. For this binary-outcome comparison, the figures are participants per arm. The general sample-size 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 as the stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the planning calculation indicates would give an 80% chance of detecting the chosen effect under those assumptions. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. Higher target power generally requires more participants, all else held constant. The sample-size table includes planning for 100%, 75%, and 50% of the observed effect; the figures rise as the assumed effect becomes smaller.

This increase has a general statistical explanation: smaller differences are harder to distinguish from random variation, so more observations are needed to estimate them with similar precision. The observed effect is the starting point for these illustrations, not a guarantee that a future study will see the same effect. When the observed difference is very small, planning around a fraction of it can produce extremely large figures, as reflected in the displayed calculations.

These numbers are not observed power. They are prospective illustrations under stated assumptions, not a measure of how likely this completed trial was to find its result after the data were collected. The registry record does not report the original sample-size justification or the assumptions used when the trial was designed.

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 = 0.984; treatment proportion p₁ = 0.983; average p̄ = 0.983.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1803 = 0.3534.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1803 = 0.1518.
4. n = (0.3534 + 0.1518)² / (-0.0004)² = 1,519,199.0, rounded up to 1,519,199 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 <- 0.983673469387755                          # control proportion
p1 <- 0.98326359832636                          # 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(3239873)
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 = 1,519,199 (80% power), 2,033,776 (90% power)
 75% of observed effect: n per arm = 2,692,570 (80% power), 3,604,586 (90% power)
 50% of observed effect: n per arm = 6,039,763 (80% power), 8,085,528 (90% power)
power.prop.test: 1519199 
Simulated power at n = 1,519,199 per arm: 0.798 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor's reported primary comparison uses the Miettinen and Nurminen method and is classified in the registry as a non-inferiority analysis. It reports a risk difference of 0.0, a 95% confidence interval from -2.7 to 2.8, and p < 0.001. The registry record also reports an exact confidence interval/binomial proportion analysis for the PE34 response rate: 98.4%, with a 95% confidence interval from 95.9% to 99.6% and p < 0.001.

The unadjusted recalculation from the posted group summary statistics gives a risk difference of -< 0.001, a 95% confidence interval from -0.023 to 0.022, and p = 0.972. It is a simple comparison of the posted proportions, not a recreation of the sponsor's non-inferiority procedure. The registry record flags a discrepancy between the recalculation and sponsor analysis. Accordingly, the sponsor's own analysis takes precedence when describing the trial's reported non-inferiority finding.

The sponsor's p-value should be interpreted as part of its non-inferiority analysis, not as an ordinary test of equality between response rates. The non-inferiority margin and the detailed analysis plan are not reported in the registry record. Without those details, the reported test cannot be fully reconstructed or independently checked from the summary statistics alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple outcome measures and analyses, as well as a range of secondary immunogenicity and safety outcomes. When a trial examines many endpoints or comparisons, multiplicity becomes relevant: repeated testing can increase the chance of a statistically notable result arising by chance. Whether and how that concern was addressed depends on the analysis plan. A multiplicity adjustment or hierarchy is not reported in the registry record.

The trial description identifies primary hypotheses involving antibody response rate, mean antibody titer, and acceptability of the response rate. The posted primary outcome is a response-rate measure. The registry record does not report the complete testing hierarchy, the non-inferiority margin, or how the distinct hypotheses were handled together. That information is necessary to understand how the confirmatory claims were controlled and how the reported p-values relate to each other.

The primary analysis population is described as participants who were seronegative at baseline and had postvaccination serology. This defines who contributed to the primary endpoint, but it does not explain how missing baseline or postvaccination measurements were handled, whether participants were excluded for other reasons, or whether sensitivity analyses were performed. Those missing-data procedures are not reported in the registry record.

The registry record also does not report the detailed statistical analysis plan, any interim analyses, the original sample-size justification, or the full set of analysis populations. It does not explain whether the analysis accounted for the multicenter design or other design features. These are unknowns, not evidence that a particular method was or was not used. They limit independent reconstruction of the sponsor's analysis and make it important to distinguish the posted sponsor results from simple recalculations based on summary statistics.

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: respiratory syncytial virus bronchiolitis (0.7%), adenovirus infection (0.3%), croup infectious (0.3%), gastroenteritis (0.3%), balanoposthitis (0.3%).

The serious adverse event figures are presented for the safety groups rather than the primary seronegative immunogenicity population. The registry reports 6 participants with serious adverse events among 299 at risk in the PE34 group, and 6 among 300 at risk in the 2016 commercial-process group. It reports 0 deaths in each group. These counts describe the posted safety data; they do not establish that the serious events were caused by vaccination.

The registry lists respiratory syncytial virus bronchiolitis at 0.7%, with adenovirus infection, infectious croup, gastroenteritis, balanoposthitis, and osteomyelitis each at 0.3% among the top serious terms. These terms are not presented as a complete account of all safety findings or as group-specific rates in the listed information.

Serious adverse events are distinct from the broader category of any adverse event. The registry also reports participants with one or more adverse events, but a serious-event count should not be treated as a count of all symptoms or reactions. The safety figures are descriptive and depend on the defined safety population and reporting period; further details of event attribution and follow-up are not reported in the registry record.

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

The primary result describes the proportion of baseline-seronegative participants who reached the specified VZV antibody threshold 6 weeks after the first vaccination. The posted response percentages are similar between the two vaccine-process groups, and the sponsor reports a non-inferiority analysis. Because the registry record flags a discrepancy between that analysis and a simple unadjusted recalculation, the sponsor's own analysis takes precedence for the trial's reported non-inferiority conclusion.

The finding is specific to the measured antibody response, the defined analysis population, the vaccination schedule, and the assessment time. It does not show how long antibody levels persist, whether participants were protected from clinical varicella, or whether the two processes have identical effects on every outcome. The primary endpoint is an immunogenicity measure, not a disease-incidence endpoint.

The trial also includes safety and tolerability outcomes, but the available serious adverse event counts alone do not establish causation or capture every aspect of safety. Interpreting safety requires the broader adverse-event results and their follow-up context. The registry record does not report all details needed to judge event attribution or the complete analysis procedures.

Non-inferiority is a margin-based statistical conclusion, not proof that two treatments are identical. The sponsor's result is labeled non-inferiority, but the margin is not reported in the registry record, making independent evaluation of that criterion incomplete. Likewise, a non-significant unadjusted comparison does not itself demonstrate equivalence or non-inferiority.

These results apply to the study setting and participants described in the registry. They do not by themselves establish that the same response rates would occur in other populations or under different schedules. The registry record does not provide an age range, detailed participant characteristics, or longer-term antibody results to extend the interpretation further.

18. Why This Trial Matters Statistically

This trial illustrates why a statistical conclusion depends not only on the observed percentages but also on the question and analysis method. A comparison of two proportions is not automatically a non-inferiority test. Non-inferiority depends on a prespecified margin, and the registry record does not report that margin. The sponsor labels its analysis as non-inferiority, while the unadjusted recalculation addresses a simpler contrast based on posted summaries.

The flagged discrepancy is an important interpretive feature. Reporting both the sponsor analysis and a transparent recalculation makes clear that these results are not interchangeable. The sponsor's analysis takes precedence for the trial's reported non-inferiority finding, while the recalculated contrast gives a direct unadjusted comparison of the posted rates. The distinction helps prevent a p-value from being detached from its method and hypothesis.

The trial also shows how the analysis population shapes an endpoint. The primary response rate concerns baseline-seronegative participants with postvaccination serology, whereas the safety data use a different group definition. An endpoint estimate is meaningful only when its population and time point are kept in view.

Finally, the study's multiple secondary outcomes make multiplicity and selective emphasis relevant. Secondary immunogenicity and safety measures can add context, but they should not be treated as equally confirmatory without a reported testing plan. For biostatisticians and clinical researchers, this record is a useful example of reading endpoint definitions, analysis populations, confidence intervals, and sponsor-reported tests together rather than interpreting any single statistic in isolation.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not report the non-inferiority margin, even though the sponsor's primary comparison is classified as a non-inferiority analysis. Without that margin and the full testing plan, the reported non-inferiority result cannot be independently reconstructed from the posted summaries. The record also flags a discrepancy between the sponsor analysis and the unadjusted recalculation, reinforcing the need to distinguish their purposes.

The primary outcome is an antibody response at 6 weeks after vaccination 1. The record does not provide a longer-term antibody assessment in the primary result, so durability cannot be evaluated from this endpoint. It also does not report a clinical varicella outcome in the primary result; antibody response should not be equated with a directly measured disease outcome.

The primary analysis is restricted to participants who were seronegative at baseline and had postvaccination serology. The registry record does not report detailed reasons for missing measurements, the approach to missing data, or sensitivity analyses. It does not provide an age range or detailed participant characteristics, limiting assessment of how closely the analyzed group represents other populations of children.

The record lists multiple outcomes and analyses but does not report a multiplicity strategy, full analysis hierarchy, or the complete statistical analysis plan. Detailed site-level or design-adjustment procedures are also not reported. The safety summary gives serious adverse event counts and selected terms, but the listed information does not provide a complete account of attribution, duration, or all event-specific comparisons.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of Immunogenicity and Safety of VARIVAX® Passage Extension 34 (PE34) Process in Children (V210-A03) — NCT03239873.
• Registry record last updated 2021-01-27; status last verified 2021-01.
• Results first posted 2019-08-26.
• 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

This completed phase 3 randomized, double-blind, multicenter, controlled study compared VARIVAX PE34 with VARIVAX made using the 2016 commercial process; both groups received M-M-R II. The primary endpoint was the percentage of baseline-seronegative participants reaching at least 5 gpELISA units/mL 6 weeks after the first vaccination.

The posted primary response estimates were 98.4% for PE34 and 98.3% for the 2016 commercial process. The sponsor reported a non-inferiority analysis, while the record flags a discrepancy with an unadjusted recalculation; the sponsor's analysis takes precedence for the reported non-inferiority finding. The registry record does not report the non-inferiority margin or complete statistical analysis plan.

Secondary outcomes covered additional immunogenicity, safety, and tolerability measures. Serious adverse event counts were 6 in each group, with 0 deaths in each group. These results should be interpreted in light of their endpoint definitions, analysis populations, and the limitations in the registry record.