Safety, Tolerability, and Immunogenicity of Measles, Mumps, Rubella, and Varicella (MMRV) Vaccine Made With an Alternative Manufacturing Process (AMP)(V221-027): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety, Tolerability, and Immunogenicity of Measles, Mumps, Rubella, and Varicella (MMRV) Vaccine Made With an Alternative Manufacturing Process (AMP)(V221-027) (NCT01536405), a randomized phase 3 study. The primary outcome is Percentage of Participants With Varicella Zoster Virus (VZV) Antibody Levels >=5 gpELISA Units/mL.

2. Clinical Question

3. Trial Design

This was a phase III, randomized, quadruple-masked, parallel-group, controlled study. Its stated purpose was to evaluate the safety, tolerability, and immunogenicity of MMRV vaccine made with an alternative manufacturing process compared with vaccine made with the 2006 manufacturing process. The registry lists an enrollment of 1412 and a completed study status. The recorded start date is 2012-06-05, and the primary completion date is 2013-07-02.

The two intervention arms were MMRV (AMP) and MMRV (2006 process). Participants in both arms received two 0.5 mL subcutaneous injections of their assigned vaccine. The registry identifies measles, mumps, rubella, and varicella as the conditions under study. It does not report further detail about the timing between injections, the randomization procedure, the concealment process, or the specific roles of those included in quadruple masking.

The primary endpoint was the percentage of participants reaching a VZV antibody level of at least 5 gpELISA Units/mL six weeks after vaccination 1. The primary population was per protocol: participants had to receive at least one dose, be seronegative at baseline, and have postvaccination VZV serology results. Thus, the endpoint denominator is narrower than overall enrollment. The registry posts 586 participants for the AMP endpoint result and 589 for the 2006-process endpoint result.

The record lists 16 outcome measures and 13 analyses, including secondary outcomes concerning fever, rashes, mumps-like symptoms, and injection-site adverse events. The detailed protocol, original sample-size justification, and full analysis plan 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.

Before assignment: One participant was inadvertently randomized twice, for a total of 1413 randomizations. The Participant Flow reported below includes this participant only once.

Randomization to Visit 1 (Vaccination 1)

Reasons for not completing this period:

Visit 1 (Vaccination 1) to Visit 2

Reasons for not completing this period:

Visit 2 to Visit 3 (Vaccination 2)

Reasons for not completing this period:

Visit 3 (Vaccination 2) to Visit 4

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The per protocol population included participants who received \>=1 dose of study vaccine, were seronegative at baseline and had postvaccination VZV serology results

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 (VZV) Antibody Levels >=5 gpELISA Units/mL, measured over Six weeks after vaccination 1.

The primary endpoint is the percentage of participants whose VZV antibody level was at least 5 gpELISA Units/mL six weeks after vaccination 1. Antibody levels were measured in serum using a glycoprotein enzyme-linked immunosorbent assay, or gpELISA. The endpoint therefore describes the proportion meeting a prespecified antibody threshold at a particular follow-up point; it is not a direct measure of clinical illness or of the duration of an antibody response.

The registry identifies the endpoint population as per protocol. Participants had to receive at least one study-vaccine dose, be seronegative at baseline, and have postvaccination VZV serology results. This population definition matters because the reported percentages apply to participants meeting those conditions, not automatically to everyone enrolled or randomized.

A threshold-based percentage offers a straightforward way to describe immunogenicity: it shows how common a defined antibody response was in each arm. The confidence interval communicates the uncertainty around each estimated percentage. The registry also reports a between-arm risk-difference analysis, which compares the response percentages directly. The record does not provide the clinical rationale for choosing the threshold, or state how this antibody endpoint relates to protection from disease; those details are not reported in the registry record.

7. Results Posted in the Registry

• MMRV (2006 Process): 93.0% (548/589) versus 97.3% (570/586) on control; risk difference -4.2 percentage points (95% CI -6.7 to -1.8), risk ratio 0.96 (0.93–0.98); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a percentage response measure?

A percentage response is the share of participants in a defined analysis population who met the endpoint criterion. In this trial, the criterion was a VZV antibody level at or above 5 gpELISA Units/mL six weeks after vaccination 1. The result reduces each participant's measured antibody level to a threshold outcome: meeting or not meeting the criterion. It does not describe the distribution of antibody levels above or below that threshold.

The population definition is essential to interpreting the percentage. The registry says the per-protocol population included participants who received at least one dose, were seronegative at baseline, and had postvaccination serology results. Therefore, the posted response rate pertains to those participants with the specified eligibility and measurement conditions. It should not be assumed to represent all enrolled participants.

What does a risk difference express?

A risk difference subtracts one group's event proportion from the other group's event proportion, using a stated group order. For a favorable response such as reaching the antibody threshold, changing the order changes the sign: the same contrast can be expressed as AMP relative to the 2006 process or as the 2006 process relative to AMP. A sign is meaningful only alongside the group order. The sponsor reported a risk difference of 4.2, with a 95% confidence interval from 1.8 to 6.8. The recalculated comparison uses the reverse ordering and is reported as -0.042, with an interval from -0.067 to -0.018.

The sponsor identifies the method as Miettinen and Nurminen for the risk difference. This is a method for estimating a confidence interval and testing a difference between proportions. The registry does not report the complete calculation details, such as any stratification or adjustment variables, so those should not be inferred from the method name alone.

How should a p-value be understood?

The sponsor reported p < 0.001 for the risk-difference analysis, and the posted recalculation also gives an unadjusted p < 0.001. In general, a p-value quantifies how incompatible the observed data are with a specified null hypothesis, under the statistical model used. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. It also does not replace the confidence interval, which gives a range of estimates compatible with the data and model.

The word unadjusted means that the recalculated p-value has not been adjusted for multiple comparisons. The registry lists 16 outcome measures and 13 analyses, but the multiplicity strategy is not reported in the registry record. It is therefore not possible to determine from the record whether the sponsor controlled an overall error rate across endpoints or analyses, or whether a particular analysis was designated as confirmatory.

What does the reported analysis population imply?

Per-protocol analyses can be useful when the question concerns responses among participants who followed key study conditions and had endpoint measurements. However, excluding participants who do not meet these conditions may affect comparability between randomized groups if exclusions are related to treatment or outcome. The registry does not report the participant flow, reasons for exclusion, or a complementary intention-to-treat analysis for this endpoint. This limits assessment of how the per-protocol result relates to the full randomized population.

In general, missing outcome data can affect estimates if the participants without measurements differ from those with measurements in ways related to response. The record does not report how missing serology results were handled, whether missingness was assessed by arm, or whether sensitivity analyses were conducted. Those details are important for judging the robustness of the endpoint estimate.

Why do the analysis method and endpoint definition matter?

The antibody result is a binary threshold outcome derived from a laboratory measurement. The percentage is easy to interpret, but it discards information about the exact antibody values. A participant just below the threshold and a participant with a much lower level are both counted as not meeting the endpoint; participants at different levels above the threshold are both counted as meeting it.

Confidence intervals for percentages and risk differences reflect sampling uncertainty under the method used. A narrower interval generally indicates greater precision for the parameter being estimated, while a wider interval indicates more uncertainty. These intervals do not account automatically for every source of uncertainty, such as bias from missing outcomes, deviations from the analysis plan, or limitations in endpoint relevance. Those issues require design and reporting information beyond the numerical interval.

The registry labels the sponsor's risk-difference analysis as non-inferiority or equivalence type. In general, non-inferiority testing asks whether a treatment is not worse than a comparator by more than a prespecified margin, while equivalence testing asks whether the difference lies within prespecified bounds in both directions. The margin or bounds, the direction of the hypothesis, and the prespecified decision procedure are not reported in the registry record. Consequently, the label alone is insufficient to reconstruct the sponsor's full inferential framework.

10. Confidence Intervals and Precision

The AMP response estimate was 97.3%, with a 95% confidence interval from 95.6% to 98.4%. The 2006-process estimate was 93.0%, with a 95% confidence interval from 90.7% to 95.0%. These intervals convey uncertainty around the respective group percentages. They are not ranges containing 95% of individual participants' antibody results.

The sponsor's between-group estimate was a risk difference of 4.2, with a 95% confidence interval from 1.8 to 6.8. The interval is entirely on the positive side of zero in the sponsor's reported orientation, and the reported p-value is p < 0.001. The recalculated contrast is expressed in the reverse group order, with an estimate of -0.042 and a 95% confidence interval from -0.067 to -0.018. The sign change reflects the order of the groups being contrasted.

Confidence intervals are useful because an estimate alone can overstate certainty. They show a range of values compatible with the data under the calculation method and its assumptions. They do not capture all possible sources of error: selection into the per-protocol population, missing serology, measurement limitations, and analysis choices may affect interpretation without being represented in the interval.

The posted intervals are relatively close to their point estimates, but precision should be considered in relation to the endpoint, analysis population, and study design. The registry record does not report the protocol details needed to assess whether the interval was the planned primary inferential basis or how it was incorporated into the study's stated non-inferiority or equivalence framework.

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 sample-size figures are planning illustrations based on the observed effect, not the trial's original design justification. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning effect is set to a stated fraction of the observed effect. The trial's original sample-size assumptions are not reported in the registry record.

For planning for 100% of the observed effect, the figures are 404 participants per arm for 80% power and 540 participants per arm for 90% power. For planning for 75% of the observed effect, they are 643 participants per arm for 80% power and 861 participants per arm for 90% power. For planning for 50% of the observed effect, they are 1,278 participants per arm for 80% power and 1,710 participants per arm for 90% power. These are participants per arm, not total enrollment or total events.

In general, power is the probability that a planned analysis will detect an effect of the chosen size if that effect is present, under the assumptions of the calculation. The 80% and 90% columns represent different target probabilities of detection; planning for the higher target requires more participants at each listed effect fraction. The displayed figures also illustrate that smaller effects need more participants to detect reliably, all else held constant.

These values are not observed power and do not describe the probability that the trial's result is correct. They are hypothetical planning requirements calculated from the observed effect under stated assumptions. They should not be taken as evidence of what the study originally planned or as a substitute for the registry's unreported design justification.

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 = 0.973; treatment proportion p₁ = 0.930; average p̄ = 0.952.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3037 = 0.5952.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3022 = 0.2543.
4. n = (0.5952 + 0.2543)² / (-0.0423)² = 403.2, rounded up to 404 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 <- 0.972696245733788                          # control proportion
p1 <- 0.930390492359932                          # 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(1536405)
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 = 404 (80% power), 540 (90% power)
 75% of observed effect: n per arm = 643 (80% power), 861 (90% power)
 50% of observed effect: n per arm = 1,278 (80% power), 1,710 (90% power)
power.prop.test: 403.2 
Simulated power at n = 404 per arm: 0.812 (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. Analyses Reported by the Sponsor

The registry reports a sponsor analysis using the Miettinen and Nurminen method for the risk difference. It gives a risk difference of 4.2, a 95% confidence interval from 1.8 to 6.8, and p < 0.001. The registry labels this as a non-inferiority or equivalence-type analysis. The record does not include the margin or full decision rule, so the reported estimate and test can be described, but the complete basis for a formal non-inferiority or equivalence conclusion cannot be reconstructed.

A simple recalculation from the posted summary statistics gives a risk difference of -0.042, a 95% confidence interval from -0.067 to -0.018, and an unadjusted p < 0.001. The recalculation orders the contrast as 2006 process relative to AMP; the sponsor's positive estimate uses the reverse orientation. This accounts for the opposite signs. The recalculation does not replace the sponsor's method or establish the sponsor's planned analysis.

The registry discrepancy indicator is false, so no discrepancy is flagged between the posted results and the recalculation. The sponsor's reported method remains the primary source for the trial's own analysis, while the recalculation is a check based on the posted summary statistics. The record does not report whether the sponsor's method included additional adjustments beyond those identified in the registry.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 16 outcome measures and 13 analyses. It identifies a primary endpoint and also lists secondary outcomes, including fever, zoster-like rash, mumps-like symptoms, measles-like rash, rubella-like rash, varicella-like rash, and injection-site adverse events. With multiple outcomes or analyses, interpreting each p-value as if it were the sole test can increase the chance of at least one apparently unusual result arising by chance. In general, multiplicity procedures can address this by adjusting tests or by defining a hierarchy of hypotheses.

The multiplicity strategy is not reported in the registry record. The record does not state whether the primary endpoint was protected from other tests through a prespecified hierarchy, whether secondary outcomes were descriptive, or whether any p-values were adjusted. The recalculated p-value is explicitly unadjusted; it should not be interpreted as controlling error across the listed outcomes and analyses.

The primary analysis population is described as per protocol, with inclusion requiring at least one dose, baseline seronegativity, and postvaccination VZV serology. The record does not report a participant flow diagram, the number excluded from each arm and reasons for exclusion, or results for an intention-to-treat population. It also does not report how missing antibody measurements were handled or whether missingness differed by arm.

In general, missing data can affect an estimate when the probability of having an observed result is related to the outcome or to the assigned intervention. Methods such as imputation or sensitivity analysis can examine the impact of assumptions about unobserved outcomes, but the registry does not describe such methods for this endpoint. The protocol's analysis plan, prespecified endpoint hierarchy, and handling of missing data are not reported in the registry record. These gaps limit assessment of whether the posted analysis follows a fully prespecified plan and how robust it is to alternative analysis choices.

15. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: febrile convulsion (0.6%), asthma (0.4%), gastroenteritis (0.3%), dehydration (0.3%), bronchiolitis (0.3%).

The registry reports serious adverse event counts for the safety groups. In the AMP group, 21 participants were affected among 682 at risk; in the 2006-process group, 18 participants were affected among 683 at risk. These are counts of affected participants and at-risk participants as posted, not percentages calculated. The record lists the most frequent serious-event terms with percentages: febrile convulsion, 0.6%; asthma, 0.4%; gastroenteritis, 0.3%; dehydration, 0.3%; bronchiolitis, 0.3%; and croup infectious, 0.3%.

These figures should be read as descriptive safety information. The registry does not provide enough detail in this record to establish the timing, duration, severity grading, or causal relationship of each event to vaccination. It also does not report deaths in the posted safety data. Serious adverse events and the listed event terms are not interchangeable measures: the serious-event counts concern participants affected, while the listed terms are reported with percentages.

Comparisons of event counts require attention to the safety population and event definitions. They do not by themselves establish whether a difference is meaningful or caused by the vaccine. The record's additional adverse-event analyses and detailed case definitions are not reproduced in these figures.

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

The primary result describes VZV antibody response at one specified time point. The posted percentage meeting the threshold was 97.3% in the AMP arm and 93.0% in the 2006-process arm, among the per-protocol participants with the required baseline and postvaccination serology conditions. The sponsor's risk-difference estimate was 4.2, with a 95% confidence interval from 1.8 to 6.8 and p < 0.001.

These results support a statistical description of the observed response percentages and their between-group contrast. They do not, on their own, establish the clinical importance of the difference. The endpoint is based on an antibody threshold, and the registry does not report how that threshold predicts protection against disease or how long responses persist. The result therefore should not be treated as a direct estimate of disease prevention.

The sponsor labels the comparison as a non-inferiority or equivalence-type analysis. A formal interpretation of that framework depends on a prespecified margin or bounds and a decision rule. Those details are not reported in the registry record. The positive risk-difference estimate and its interval can be described as posted, but the record alone does not permit full independent verification of the formal claim underlying the label.

The primary endpoint result is not a safety conclusion. Safety information is reported separately, with serious adverse events affecting 21 participants among 682 at risk in the AMP group and 18 among 683 at risk in the 2006-process group. The posted counts and event terms are descriptive and do not prove causation or resolve the comparative safety profile.

Finally, the per-protocol result does not necessarily represent every randomized participant. The registry does not report missing-data handling, exclusions by reason, or a complementary intention-to-treat result for this endpoint. These limitations matter when judging how broadly the posted response percentages can be generalized.

17. Why This Trial Matters Statistically

This trial raises a useful statistical distinction between a measured biological response and a clinical outcome. Its primary endpoint is a threshold-based antibody percentage, rather than a direct count of illness. Such endpoints are common in immunogenicity studies because they summarize laboratory response in a clinically interpretable format, but their meaning depends on the threshold and its relationship to protection. That relationship is not reported in the registry record.

The comparison also illustrates why a group contrast must be read with its direction and method. The same between-group difference changes sign when the order of groups is reversed. The sponsor's positive risk difference and the recalculated negative risk difference express opposite orderings, not opposing findings. The group labels, interval, and analysis method are necessary context for interpreting the estimate.

Precision and formal testing answer related but distinct questions. The confidence interval shows uncertainty around the estimated contrast, while the p-value evaluates compatibility with a null model under the chosen test. Neither establishes clinical importance. In a non-inferiority or equivalence framework, the margin and prespecified rule are central; those details are not reported in the registry record, limiting independent assessment of the formal claim.

The record also highlights the importance of analysis populations and transparency about missing data. The endpoint uses a per-protocol population with specified serology conditions. Without participant flow and missing-data details, readers cannot fully assess how selection into that analysis may have affected the estimate. Together, these issues show why a statistically clear antibody response comparison still requires careful attention to design, endpoint validity, and reporting.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary endpoint is a laboratory antibody threshold at six weeks after vaccination 1. The registry does not report the clinical rationale for the threshold or its relationship to protection from measles, mumps, rubella, or varicella disease. Nor does this endpoint, by itself, describe antibody levels over longer follow-up.

The analysis population is per protocol and requires at least one dose, baseline seronegativity, and a postvaccination serology result. The registry does not report participant exclusions by arm, reasons for exclusion, missing serology handling, or an intention-to-treat result for the primary endpoint. This limits assessment of possible selection effects and the influence of missing outcomes.

Although the sponsor's analysis is labeled as non-inferiority or equivalence type, the margin, hypothesis formulation, and prespecified decision rule are not reported in the registry record. The original sample-size justification and the trial's original statistical analysis plan are also not reported. The planning illustrations based on the observed effect cannot substitute for those original design details.

The registry lists multiple outcomes and analyses, but does not report a multiplicity strategy. It also does not provide sufficient detail to assess randomization implementation, allocation concealment, masking roles, or whether the reported analysis incorporated any adjustments. These are limitations of the available record rather than evidence that the study procedures were inadequate.

Safety figures are posted as affected-participant counts and selected event-term percentages, but further details about event timing, grading, attribution, and follow-up are not reported in the registry record. The safety numbers should therefore be interpreted descriptively and not as proof of causation.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety, Tolerability, and Immunogenicity of Measles, Mumps, Rubella, and Varicella (MMRV) Vaccine Made With an Alternative Manufacturing Process (AMP)(V221-027) — NCT01536405.
• Registry record last updated 2018-10-31; status last verified 2018-10.
• Results first posted 2014-07-02.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01536405 is a completed phase III randomized, quadruple-masked, parallel-group controlled study of MMRV vaccine made with an alternative manufacturing process versus the 2006 manufacturing process. Enrollment was 1412. Participants received two 0.5 mL subcutaneous injections of their assigned vaccine.

The primary outcome was the percentage with VZV antibody levels at or above 5 gpELISA Units/mL six weeks after vaccination 1. The per-protocol response estimates were 97.3% for AMP and 93.0% for the 2006 process. The sponsor reported a risk difference of 4.2, with a 95% confidence interval from 1.8 to 6.8 and p < 0.001.

The registry also posts secondary outcomes and serious adverse-event information. The non-inferiority or equivalence margin, multiplicity approach, original sample-size justification, and detailed missing-data methods are not reported in the registry record.