Rapid Immunization Study of the Japanese Encephalitis Vaccine IC51: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Rapid Immunization Study of the Japanese Encephalitis Vaccine IC51 (NCT00595790), a randomized phase 3 study. The primary outcome is SCR (Seroconversion Rate) at Day 56.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, single-masked, parallel study of IC51 for Japanese encephalitis. The registry record lists an enrollment of 374 and describes the participants as healthy subjects aged 18 years or older. The study began in 2005-09, reached primary completion in 2006-02, and is marked completed. The sponsor is Valneva Austria GmbH.

The arm descriptions identify IC51 2 x 6 mcg, IC51 1 x 12 mcg, and IC51 1 x 6 mcg. The study title describes a comparison of a rapid immunization regimen with a standard regimen. The registry comparison designates IC51 1 x 12 mcg as the control for the recalculated contrasts. The record does not give further detail on the dose timing or the interval between administrations, so the schedules should not be inferred beyond their arm labels.

Randomization indicates that allocation to study regimens was assigned by chance, while parallel design means participants were assigned to a regimen rather than crossing between regimens. The masking field is recorded as single, but which parties were masked is not reported in the registry record. Details of sequence generation, allocation concealment, and the original sample-size justification are also not reported in the registry record.

The primary outcome was assessed at Day 56 in the Per-Protocol-Population, described as randomized subjects without major protocol deviation. Participant flow is described as showing all randomized participants, but the record does not give the reasons for any exclusions from the per-protocol analysis. Secondary outcomes listed include seroconversion rate at Day 10, 28, and 35; geometric mean titer at Day 10, 28, 35, and 56; and safety.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: The Participant Flow shows all study participants randomized. The Primary Outcome is based on the Per-Protocol-Population (all randomized subjects without major protocol deviation

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 SCR (Seroconversion Rate) at Day 56, measured over day 56.

The primary endpoint is the seroconversion rate at Day 56: the percentage of participants with an anti-JEV neutralizing antibody titer of at least 1:10. This is a binary outcome at the participant level: each participant either meets the stated antibody threshold or does not. Reporting it as a percentage expresses how common that outcome was in each regimen group.

Seroconversion is an immunogenicity measure. It records whether an antibody response reaches the threshold specified in the registry record. It is not itself a measure of clinical Japanese encephalitis cases, symptoms, or protection from disease. The registry record does not report a clinical disease endpoint as the primary outcome.

A fixed assessment time matters because the percentage is tied to the stated follow-up point. The primary endpoint is at Day 56, while the listed secondary seroconversion assessments occur at Day 10, 28, and 35. The geometric mean titer outcome, also listed at several time points, describes antibody levels differently from the threshold-based seroconversion percentage. Neither endpoint definition alone establishes how antibody results relate to clinical outcomes.

The primary outcome is based on the Per-Protocol-Population, which the registry describes as randomized subjects without major protocol deviation. This makes the interpretation dependent on the participants included in that population, not solely on the randomized participant flow. The record does not report detailed rules for the threshold assessment, handling of missing antibody measurements, or the exact criteria for a major protocol deviation.

7. Results Posted in the Registry

• IC51 2x6 mcg: 97.4% (112/115) versus 40.9% (47/115) on control; risk difference 56.5 percentage points (95% CI 47.1 to 66.0), risk ratio 2.38 (1.91–2.97); unadjusted two-proportion z-test p = <0.001.
• IC51 1x6 mcg: 25.2% (30/119) versus 40.9% (47/115) on control; risk difference -15.7 percentage points (95% CI -27.6 to -3.8), risk ratio 0.62 (0.42–0.90); unadjusted two-proportion z-test p = 0.011.

8. Statistical Interpretation

9. Statistical Methods Explained

For a binary outcome such as seroconversion, each participant contributes an outcome that meets or does not meet the stated threshold. The reported percentage is the fraction of assessed participants who meet it. A confidence interval describes uncertainty around an estimate: it gives a range of values that are compatible with the data under the method's assumptions. It is not a range containing a known fixed percentage of individual participants, and it does not account for every possible source of bias.

What does the unadjusted comparison represent?

The recalculated contrasts are unadjusted risk differences. In general, a risk difference is the outcome proportion in one group minus the outcome proportion in the comparison group. It expresses the absolute difference in outcome frequency, not a relative change. The recalculations use the posted summary counts and denominators and do not adjust for other participant characteristics or study features. They are therefore distinct from a model-based, stratified, or sponsor-specified analysis.

The recalculated p-values indicate how incompatible the observed comparison is with a null hypothesis of no difference under the simple test's assumptions. They do not give the probability that the null hypothesis is true, and they do not measure the size or practical importance of an effect. The record identifies these p-values as unadjusted. Since the registry record flags a discrepancy, the sponsor's own analysis takes precedence over these simple re-calculations.

What does the sponsor's analysis label mean?

The sponsor reports a Mantel Haenszel method for the comparison of IC51 2 x 6 mcg with IC51 1 x 12 mcg, and classifies it as a non-inferiority or equivalence analysis. In general, the Mantel Haenszel approach can combine information across strata when data are organized into strata. The registry record does not state what strata were used or provide enough methodological detail to determine how the method was implemented. Those details are not reported in the registry record.

Non-inferiority and equivalence are not ordinary tests for any difference. In general, non-inferiority asks whether an intervention is not worse than a comparator by more than a prespecified margin; equivalence asks whether the difference lies within prespecified margins in both directions. Interpretation therefore depends on the margin, the analysis population, the effect estimate, and its uncertainty. The registry record gives p > 0.99 but does not report the margin, estimate, confidence interval, or direction of the test. The p-value should not be read as proof of equivalence or non-inferiority without those details.

Why might over-dispersion matter?

General: over-dispersion occurs when observed variability is greater than a statistical model expects. It can make standard errors too small if the model does not account for that extra variability. The primary outcome is a participant-level binary percentage, and no over-dispersion assessment or model-based adjustment is reported in the registry record. This concept should not be taken as a claim that over-dispersion occurred in this study.

Why does the analysis population matter?

The registry identifies the Per-Protocol-Population as the primary outcome population and describes it as randomized subjects without major protocol deviation. A per-protocol analysis excludes participants who do not meet the relevant protocol criteria. In general, this can make an analysis sensitive to the reasons for exclusion and to whether those exclusions relate to treatment assignment or outcome. The record does not give the number or reasons for any exclusions, nor does it report a corresponding intention-to-treat estimate for the primary endpoint. The participant flow is described as showing all randomized participants, but that description does not replace the details needed to understand the per-protocol analysis set.

What is not documented?

The registry record does not report the original sample-size justification, the full statistical analysis plan, interim analyses, missing-data procedures, or multiplicity adjustment. It also does not provide all details of the sponsor's test. These absences mean that the reported outcome and p-values can be described, but the unreported design and analysis choices cannot be reconstructed. General statistical principles can help explain what the methods mean; they cannot fill in those study-specific details.

10. Confidence Intervals and Precision

The posted 95% confidence intervals give a sense of the precision of each Day 56 seroconversion percentage. For IC51 1 x 12 mcg, the estimate is 41.2% with a 95% confidence interval from 32.2% to 50.3%. For IC51 2 x 6 mcg, it is 97.3%, with an interval from 94.4% to 100.0%. For IC51 1 x 6 mcg, it is 25.6%, with an interval from 17.7% to 33.6%. These intervals quantify sampling uncertainty under the method used; they do not cover all uncertainty from study conduct, population selection, or analysis choices.

In general, a confidence interval is more informative than a point estimate alone because it displays a range of uncertainty around the estimated percentage. A narrower interval indicates greater precision under the calculation's assumptions; a wider interval indicates less precision. An interval reaching 100.0% also reflects the natural upper boundary for a percentage. The intervals do not say that every value inside the range is equally plausible, and they are not a guarantee that the true value falls within the interval.

The sponsor's reported non-inferiority or equivalence analysis has no estimate or confidence interval recorded, so its precision cannot be judged from the sponsor result. The registry record reports p > 0.99, but a p-value does not show the range of effects compatible with the data. The unadjusted re-calculations include contrast intervals in the underlying analysis, but the record also flags a discrepancy; the sponsor analysis therefore takes precedence. The arm-level intervals remain useful descriptions of uncertainty in the posted percentages, but they do not resolve the missing details of the sponsor's comparison.

These intervals pertain to seroconversion at Day 56 in the reported analysis population. They should not be interpreted as confidence intervals for clinical disease prevention, safety, or outcomes at other time points.

11. Planning a Similar Trial: Sample Size

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

The planning estimates are illustrations for a future two-arm comparison, not the number enrolled in this completed study. The figures are participants per arm, not total participants and not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses a stated fraction of the observed effect: 100%, 75%, or 50% of that effect. The effect used is based on the observed comparison in the posted results, and the original trial's own design assumptions are not reported in the registry record.

The 80% power column gives the illustrated participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect is the true one and the assumptions hold. The 90% power column gives the corresponding participants per arm for a design with a 90% chance under those same assumptions. These are planning quantities, not guarantees about a future study's outcome. The sample-size illustration is not observed power.

The rows that use a smaller fraction of the observed effect require more participants per arm in the displayed estimates. This is the usual planning relationship: smaller effects are harder to distinguish from random variation, so more information is needed. The required numbers also differ between the two displayed comparisons because they use different observed effects. They should not be treated as interchangeable across endpoints or as a reconstruction of why the registry trial enrolled its participants.

For the IC51 2 x 6 mcg comparison, planning for 100% of the observed effect gives 10 participants per arm for 80% power and 12 for 90% power; planning for 75% gives 20 and 26; planning for 50% gives 48 and 64. For the IC51 1 x 6 mcg comparison, the corresponding figures are 141 and 188; 258 and 345; and 596 and 797. These estimates follow the stated assumptions and are not observed trial results.

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 = 0.409; treatment proportion p₁ = 0.974; average p̄ = 0.691.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6533 = 1.2805.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5168 = 0.4349.
4. n = (1.2805 + 0.4349)² / (0.5652)² = 9.2, rounded up to 10 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 <- 0.408695652173913                          # control proportion
p1 <- 0.973913043478261                          # 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(595790)
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 = 10 (80% power), 12 (90% power)
 75% of observed effect: n per arm = 20 (80% power), 26 (90% power)
 50% of observed effect: n per arm = 48 (80% power), 64 (90% power)
power.prop.test: 9.2 
Simulated power at n = 10 per arm: 0.858 (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 Mantel Haenszel method for IC51 2 x 6 mcg compared with IC51 1 x 12 mcg. It is classified as a non-inferiority or equivalence analysis and has a reported p-value of p > 0.99. The record does not give the sponsor's effect estimate, confidence interval, test margin, or further explanation of the analysis.

The unadjusted recalculations are simple comparisons from the posted summary statistics. They are not the sponsor's analysis and should not be used to replace it. The registry record flags a discrepancy, so the sponsor's own analysis takes precedence. In particular, the recalculated risk-difference p-value should not be used to overturn, reinterpret, or restate the sponsor's non-inferiority or equivalence analysis.

The reported p-value alone does not establish that the regimens are equivalent or that a non-inferiority condition was met. Such an interpretation requires the prespecified margin and the relevant estimate and uncertainty, which are not reported in the registry record. The sound reading is therefore limited: the sponsor recorded a Mantel Haenszel non-inferiority or equivalence analysis and a p-value greater than 0.99, while the details needed to assess the substantive conclusion are absent.

14. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is seroconversion rate at Day 56. The registry also lists seroconversion assessments at Day 10, 28, and 35, geometric mean titer at Day 10, 28, 35, and 56, and safety outcomes. Multiple outcomes, time points, and regimen comparisons create opportunities for multiple statistical testing. In general, when many hypotheses are examined, the chance of at least one apparently unusual result can increase unless the analysis plan accounts for multiplicity.

Whether and how multiplicity was handled is not reported in the registry record. The record lists one reported analysis, but that count does not establish that only one analysis was conducted or that adjustment was unnecessary. No hierarchy of endpoints, prespecified testing sequence, or multiplicity adjustment method is reported. The recalculated p-values are explicitly unadjusted and should be understood in that light.

The primary outcome population is described as the Per-Protocol-Population, consisting of randomized subjects without major protocol deviation. Participant flow is described as showing all randomized participants, but the registry does not report the detailed membership of the per-protocol set or reasons for any exclusions. The record also does not report missing-data rules for participants without an antibody measurement at Day 56, nor does it describe sensitivity analyses for missing outcomes.

These omissions matter because analysis population and missing-data handling can affect the estimate and its uncertainty. In general, excluding participants or using assumptions to handle absent measurements may change the interpretation, depending on why the data are missing and how exclusions are determined. No particular missingness mechanism or bias can be inferred from the available record. The original analysis plan, interim analyses, and sample-size justification are also not reported in the registry record, so none should be assumed.

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: chest pain (0.8%).

The registry safety entries report serious adverse events affecting 0 participants in the IC51 2 x 6 mcg group, 1 participant in the IC51 1 x 12 mcg group, and 0 participants in the IC51 1 x 6 mcg group. The corresponding serious-event populations at risk are 125, 125, and 124. The record also lists other adverse events affecting 78, 82, and 78 participants, respectively, among those at risk. These are registry counts; they are not calculated percentages.

Chest pain is listed as the top serious adverse event term, at 0.8%. The record does not give a group-specific breakdown for that term. Deaths are recorded as null, so death information is not reported in the registry record. The record does not provide further detail about event severity, duration, relationship to the vaccine, or the method used to summarize events.

These entries describe reported safety counts within the listed risk populations. They do not establish whether an event was caused by a regimen, and the figures should not be interpreted as a comprehensive safety assessment. Comparisons of event counts also require attention to the populations monitored and the completeness of reporting, details not fully available in the registry record.

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

The posted results describe the proportion of participants meeting the defined antibody threshold at Day 56 for each IC51 regimen. The reported percentages are 41.2% for IC51 1 x 12 mcg, 97.3% for IC51 2 x 6 mcg, and 25.6% for IC51 1 x 6 mcg. Their confidence intervals communicate uncertainty in those group estimates. The outcome is seroconversion, not a count of Japanese encephalitis cases or a direct measure of clinical protection.

The simple recalculations compare the observed percentages using unadjusted risk differences. They are not the sponsor's full analysis. Because the registry record identifies a discrepancy, the sponsor's own analysis takes precedence. The sponsor's reported comparison is classified as non-inferiority or equivalence, but its estimate, uncertainty, and margin are not reported. The recorded p-value by itself cannot establish equivalence, non-inferiority, or the size of any difference.

Interpretation is also limited by the analysis population. The primary outcome is based on a per-protocol population of randomized participants without major protocol deviation, and the record does not give the reasons or counts for exclusions. The record does not describe how missing Day 56 antibody results were handled, or whether multiplicity was addressed across the listed time points and outcomes. These are uncertainties about the analysis, not evidence that a particular bias occurred.

The results therefore support a description of reported immunogenicity percentages and the statistical uncertainty attached to them. They do not establish that one regimen prevents disease, does not prevent disease, or is clinically preferable. They also do not provide enough detail to independently verify the sponsor's non-inferiority or equivalence conclusion. Safety entries should likewise be read as reported event counts rather than proof of causation or a complete characterization of risk.

17. Why This Trial Matters Statistically

This trial is statistically notable because its primary outcome is a threshold-based antibody response rather than a clinical disease event. That distinction affects what the estimates mean: they quantify the proportion crossing a specified antibody threshold at Day 56. A clear endpoint definition helps prevent an immunogenicity result from being mistaken for evidence about disease incidence or clinical protection.

The comparison also illustrates how analysis choices can shape interpretation. The registry reports a sponsor Mantel Haenszel analysis classified as non-inferiority or equivalence, while simple unadjusted re-calculations are available from summary statistics. These are not interchangeable procedures. The registry's discrepancy flag and the absence of the sponsor estimate, confidence interval, and margin make it important to distinguish a recalculated contrast from the sponsor's intended inferential question.

The study also highlights the value of reporting analysis populations and uncertainty. The primary outcome uses a per-protocol population, while participant flow is described for all randomized participants. Without details of exclusions and missing outcome handling, readers cannot fully assess how the analysis set relates to randomization. Arm-level confidence intervals help show sampling precision, but they cannot address those unreported design and analysis details.

Finally, the sample-size illustrations show how planning depends on the effect one aims to detect and the assumptions used. They are not a record of the original study's rationale. Keeping planning illustrations separate from observed trial evidence avoids treating retrospective calculations as proof that a study was adequately powered for its original question.

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 registry record gives limited detail about how the study was conducted and analyzed. It records randomization, single masking, and a parallel model, but does not identify who was masked or describe sequence generation and allocation concealment. The arm labels identify dose amounts, but the timing and spacing of administrations are not reported in the registry record.

The primary analysis population is described as randomized subjects without major protocol deviation, but the record does not specify the criteria for major deviations, the number excluded, or the reasons for exclusion. Although participant flow is described as showing all randomized participants, that does not provide the details needed to evaluate how the per-protocol population was formed. Missing-data procedures for antibody outcomes are not reported.

The sponsor's reported analysis lacks an effect estimate, confidence interval, and non-inferiority or equivalence margin. The registry record flags a discrepancy between the sponsor analysis and the simple unadjusted recalculations; the sponsor analysis takes precedence, but its substantive conclusion cannot be independently assessed from the recorded information alone. Multiplicity procedures, interim analyses, the original sample-size justification, and the full statistical analysis plan are also not reported.

The primary endpoint is an antibody threshold at Day 56. The registry record does not report a primary clinical disease endpoint, so these results cannot be interpreted as direct evidence about disease occurrence. Safety reporting includes event counts and a serious-event term but lacks additional detail on event attribution and duration; deaths are not reported in the registry record. These limitations restrict interpretation without establishing that any particular problem occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Rapid Immunization Study of the Japanese Encephalitis Vaccine IC51 — NCT00595790.
• Registry record last updated 2014-04-29; status last verified 2014-04.
• Results first posted 2014-03-26.
• 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.

22. Record Summary

NCT00595790 is a completed randomized, single-masked, parallel Phase 3 study of IC51 for Japanese encephalitis, sponsored by Valneva Austria GmbH. The registry record lists enrollment of 374 and healthy subjects aged 18 years or older. The study began in 2005-09 and reached primary completion in 2006-02.

The primary outcome is seroconversion at Day 56, defined as the percentage with an anti-JEV neutralizing antibody titer of at least 1:10. It is based on a Per-Protocol-Population described as randomized subjects without major protocol deviation. The posted percentages are 41.2% for IC51 1 x 12 mcg, 97.3% for IC51 2 x 6 mcg, and 25.6% for IC51 1 x 6 mcg.

The sponsor reports a Mantel Haenszel non-inferiority or equivalence analysis for IC51 2 x 6 mcg versus IC51 1 x 12 mcg, with p > 0.99. Because a discrepancy is flagged, the sponsor analysis takes precedence over the unadjusted recalculations. The record does not report the sponsor estimate, confidence interval, or margin, limiting interpretation of that result.