Safety and Immunogenicity of the Japanese Encephalitis Vaccine IC51 (IXIARO®) in a Pediatric Population: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Immunogenicity of the Japanese Encephalitis Vaccine IC51 (IXIARO®) in a Pediatric Population (NCT01041573), a randomized phase 3 study. The primary outcome is Rate of Subjects With Serious Adverse Events and Medically Attended Adverse Events Until Day 56 After First Vaccination.

2. Clinical Question

3. Trial Design

The registry describes a randomized, open-label, active-controlled, parallel Phase 3 study. It lists enrollment of 1869 and a completed status. The study began in 2010-03, with primary completion in 2011-02. The sponsor was Valneva Austria GmbH.

IC51 was studied at two dose levels: 3 mcg in 0.25 mL and 6 mcg in 0.5 mL, administered intramuscularly on day 0 and day 28. The active controls were age-specific. Prevnar was used for children younger than 1 year, while Havrix 720 was used for participants aged 1 year and above. The primary outcome description specifies IC51 0.25 mL for the safety comparisons. The registry also lists Havrix 720 at day 0 and month 7, and Prevnar schedules involving day 0 and later doses through month 7 to month 13.

Open-label means that masking was not used, according to the registry. Random allocation indicates that participants were assigned to treatment groups by a randomized process, but details of how allocation was generated or concealed are not reported in the registry record. The record does not state the randomization ratio or describe site-level procedures. Although the trial title and secondary outcomes include immunogenicity, the primary objective was to assess local and systemic safety through Month 7 after the first IC51 vaccination.

The registry identifies age as the basis for choosing the active comparator. This matters for interpreting the results: the younger and older groups were not all compared with the same control vaccine. The registry record does not report the original sample-size justification, the planned statistical analysis details beyond the described endpoint, or interim analyses.

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: As specified per protocol, safety parameters were compared between treatment groups (i.e. IC51 any dose level versus Havrix or Prevnar), stratified by age. Age was the determining factor of the respective safety comparators Prevnar (\<1yrs) and HAVRIX (1+ yrs). Different dose levels of IC51 were grouped for these analyses, to test the hypothesis that events do not occur in higher frequency after vaccination with IC51 compared to vaccination with Prevnar® or Havrix®720.

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 Rate of Subjects With Serious Adverse Events and Medically Attended Adverse Events Until Day 56 After First Vaccination, measured over until Day 56.

The primary endpoint measures the percentage of participants with serious adverse events and medically attended adverse events through Day 56 after the first vaccination. It is a binary outcome at the participant level: each participant either had an event meeting the endpoint definition during that interval or did not. The endpoint description says comparisons were made against the respective control vaccine and stratified by age.

Safety trials use outcomes of this kind to describe how often clinically important events occur during a defined period after vaccination. Including medically attended events captures events that led to medical care, while serious adverse events represent a separate seriousness category. The registry does not provide further operational definitions of either category, so the precise criteria used to classify individual events are not reported in the registry record.

The endpoint is reported as a percentage of participants, with a 95% confidence interval. Those figures describe the observed frequency and the uncertainty around it. They do not by themselves establish that a vaccine caused an event: events occurring after vaccination may have other causes, and an active-control comparison is needed to put frequencies in context. The endpoint also does not measure protection against Japanese encephalitis. Immunogenicity is addressed separately through secondary outcomes such as neutralizing antibody titers and seroconversion.

7. Results Posted in the Registry

• Havrix 720: 14.2% (56/394) versus 16.1% (206/1280) on control; risk difference -1.9 percentage points (95% CI -5.9 to 2.1), risk ratio 0.88 (0.67–1.16); unadjusted two-proportion z-test p = 0.369.
• IC51, Subjects Aged >= 2 Months to <1 Year: 38.2% (50/131) versus 16.1% (206/1280) on control; risk difference 22.1 percentage points (95% CI 13.5 to 30.6), risk ratio 2.37 (1.84–3.05); unadjusted two-proportion z-test p = <0.001.
• Prevnar: 42.2% (27/64) versus 16.1% (206/1280) on control; risk difference 26.1 percentage points (95% CI 13.8 to 38.4), risk ratio 2.62 (1.92–3.58); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Rate of Subjects With Solicited Local and Systemic AEs

• 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:
  • Havrix 720: 29.4% (116/394) versus 40.8% (522/1280) on control; risk difference -11.3 percentage points (95% CI -16.6 to -6.1), risk ratio 0.72 (0.61–0.85); unadjusted two-proportion z-test p = <0.001.
  • IC51, Subjects Aged >= 2 Months to <1 Year: 58.0% (76/131) versus 40.8% (522/1280) on control; risk difference 17.2 percentage points (95% CI 8.4 to 26.1), risk ratio 1.42 (1.21–1.67); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Havrix 720 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for IC51, Subjects Aged >= 2 Months to <1 Year than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes covering antibody geometric mean titers, seroconversion, serious and medically attended adverse events, solicited local and systemic adverse events, unsolicited adverse events, and abnormal laboratory parameters. These outcomes broaden the study's scope beyond the primary safety endpoint, but the posted record does not give numerical results for every listed measure in the material. Consequently, the secondary results cannot be combined into a complete summary of immunogenicity and safety.

The posted solicited local and systemic adverse-event results describe events during the 7 days after vaccination. Their overall pattern varies by age group and comparator, as may be expected when event frequencies are assessed in separate populations and after different vaccine schedules. These observations provide additional context about short-term reported events; they do not directly answer the primary question about serious and medically attended events through Day 56.

Secondary outcomes can help characterize different aspects of a trial, but multiple outcomes create more opportunities for apparently notable findings. Unless a statistical plan specifies how multiple comparisons are handled, unadjusted secondary p-values carry less weight than a prespecified primary analysis. The registry record does not report a multiplicity adjustment strategy. Nor does it provide the full set of secondary numerical results needed to judge consistency across all outcomes. The secondary findings should therefore be viewed as supporting context rather than as a single confirmatory conclusion.

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

• Geometric Mean Titers (GMT) for JEV Neutralizing Antibodies
• Seroconversion Rate (SCR) at Days 0, 56 and at Month 7
• Rate of Subjects With SAEs and Medically Attended AEs
• Rate of Subjects With Solicited Local and Systemic AEs
• Rate of Subjects With Unsolicited AEs up to Day 56 and up to Month 7
• Rate of Subjects With Abnormal Laboratory Parameters

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports Fisher's exact test for its two primary comparisons. This test is designed for categorical outcomes, such as whether a participant did or did not experience an event. It compares the event counts between groups and is often used when the data are expressed as a two-by-two table. The registry does not report additional model terms or adjustment variables for these analyses.

What does the percentage measure?

The endpoint is a participant-level event rate, expressed as a percentage. It answers what fraction of participants in a treatment group experienced an event meeting the endpoint definition during the stated follow-up. The rate is not an event count per unit of time, and it does not indicate how many separate events each affected participant experienced. Repeated events and time to first event are not described in the primary outcome definition.

In general, a between-group risk difference expresses the difference between two event probabilities on the absolute scale. A risk ratio expresses their relative frequency. These are different ways of describing a contrast and answer different questions: an absolute contrast concerns how far apart the rates are, while a relative contrast concerns how many times as frequent one rate is compared with another. The posted recalculations are simple, unadjusted calculations from summary statistics; they do not account for the age-stratified sponsor analysis.

Why does the age-stratified comparison matter?

The registry specifies different active controls according to age: Prevnar for participants younger than 1 year and Havrix for participants aged 1 year and above. This is not a single common-control design across all participants. Age groups may differ in their underlying event frequencies, so comparisons across age strata should not be treated as though they were randomized comparisons between the same populations. The relevant primary comparisons are IC51 versus the age-specific control within each stratum.

The recalculated comparisons use summary counts and are unadjusted. They are not the sponsor's reported stratified Fisher analyses. A recalculation based on aggregate data may not reproduce a sponsor analysis when the analysis population, grouping, or stratification differs. The exact source of the discrepancy is not reported in the registry record; the sponsor's own analysis therefore takes precedence when describing the trial's reported inference.

How should p-values be understood?

A p-value measures how unusual data at least as incompatible with a null hypothesis as the observed data would be, if that null hypothesis and the test assumptions held. A small p-value does not measure the size of a difference or its importance, and a large p-value does not prove that the groups are identical. For this study, the sponsor's p-values should be read together with the arm-level rates and confidence intervals, not as stand-alone conclusions.

Fisher's exact test is a method for comparing categorical outcomes. Unlike a large-sample approximation, it calculates probabilities based on the observed group counts under the null model. The registry names the method but does not report whether tests were one- or two-sided, the exact analysis population, or further details about test implementation. Those aspects are not reported in the registry record.

Why do confidence intervals accompany rates?

A confidence interval gives a range of values compatible with the observed data under the interval method. For each group, the reported 95% confidence interval conveys uncertainty around the estimated event percentage. Wider intervals indicate less precision, often because the available information is limited. The intervals are not a guarantee that the true value lies within the displayed range, and the interval for each arm is not itself a direct interval for the between-group difference.

The posted recalculated comparisons include unadjusted interval estimates and p-values, but these are not equivalent to the sponsor's reported age-stratified inference. Where the registry record reports a sponsor result that differs from a simple recalculation, the sponsor analysis takes precedence. The recalculated figures can be useful as an independent descriptive check, but should not be presented as the trial's own analysis.

What is not specified?

The registry record does not report the original sample-size justification, allocation concealment, the planned statistical analysis plan in detail, interim analyses, missing-data methods, or a multiplicity adjustment strategy. It also does not provide enough detail to assess all assumptions behind the analysis or to determine whether every outcome was analyzed in the population originally intended. These omissions do not negate the posted results, but they restrict independent assessment of the analysis choices.

11. Confidence Intervals and Precision

The primary arm-level estimates have different levels of precision across age groups. For participants aged 1 year and above, the reported 95% confidence interval was 14.1% to 18.2% for IC51 and 10.9% to 18.1% for Havrix 720. For participants aged 2 months to younger than 1 year, the corresponding intervals were 29.8% to 47.1% for IC51 and 29.9% to 55.2% for Prevnar. The younger-group intervals are wider, consistent with the smaller group sizes recorded for that stratum.

In general, a confidence interval communicates statistical uncertainty in an estimated rate. It does not capture every source of uncertainty, such as uncertainty about outcome classification, follow-up completeness, or whether the study population represents other settings. The registry record does not give enough information to assess these issues fully.

Arm-specific intervals should not be mistaken for a confidence interval on the difference between arms. A formal interval for a contrast directly addresses uncertainty in that contrast. The recalculated comparisons include unadjusted contrast intervals, but the registry's sponsor analyses are age-stratified and take precedence where the recalculation differs. In particular, the sponsor's reported inference should not be displaced by a comparison constructed from aggregate counts.

Interval overlap is not a reliable substitute for a formal comparison. Two arm-specific intervals may overlap even when a test of the between-group contrast gives a small p-value, or may have little overlap without directly quantifying the contrast. Interpretation should consider the design, the specified comparator, the sponsor's analysis, and the precision of the estimates together.

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 expressed as participants per arm. The endpoint is a participant-level binary outcome, so these figures are not total event counts. The illustrations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They use the observed effect as a reference and show planning for 100%, 75%, and 50% of that effect. The original trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a design intended to detect the stated effect under those assumptions with 80% power. The 90% power column gives the corresponding number for 90% power. Power is a design property under assumed conditions; it is not the probability that a result is true. Smaller effects require more participants to detect than larger effects under otherwise similar assumptions. For example, the entries for planning for 50% of the observed effect are larger than the entries for planning for 100% of the observed effect.

These values are not observed power. They do not establish whether the completed study was adequately powered for its original objectives because the original design assumptions are not reported. They are recalculated planning examples based on the observed effect, and a different underlying effect or design assumption would yield different planning requirements.

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 = 0.161; treatment proportion p₁ = 0.142; average p̄ = 0.152.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5071 = 0.9939.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5069 = 0.4266.
4. n = (0.9939 + 0.4266)² / (-0.0188)² = 5,705.9, rounded up to 5,706 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 <- 0.1609375                          # control proportion
p1 <- 0.142131979695431                          # 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(1041573)
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 = 5,706 (80% power), 7,639 (90% power)
 75% of observed effect: n per arm = 10,274 (80% power), 13,753 (90% power)
 50% of observed effect: n per arm = 23,405 (80% power), 31,333 (90% power)
power.prop.test: 5705.9 
Simulated power at n = 5,706 per arm: 0.799 (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 registry reports Fisher exact tests for the sponsor's age-specific primary comparisons. For participants aged 2 months to younger than 1 year, the comparison of IC51 with Prevnar had p = 0.641. For participants aged 1 year and above, the comparison of IC51 with Havrix 720 had p < 0.001.

The simple recalculations are not a replacement for these analyses. The recalculated comparisons are unadjusted, and their group construction does not consistently reproduce the sponsor's age-stratified comparisons. For the older IC51-versus-Havrix comparison, the recalculated p-value is 0.369, which differs from the sponsor's reported p-value. The discrepancy is flagged in the posted results. The sponsor's own analysis takes precedence when stating the trial's reported inferential result.

This precedence does not mean that the recalculation is meaningless. It highlights that summary-statistic calculations can depend on which groups are contrasted and how the analysis handles the design. The recalculation should be interpreted as a separate, unadjusted check rather than an alternative sponsor result. The registry record does not explain the source of the discrepancy or provide enough analysis detail to reconcile it further.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint includes two age-specific comparisons, each using a different active control. The registry reports a Fisher exact test for each comparison, but a strategy for controlling the chance of false-positive findings across those tests is not reported in the registry record. The record also lists multiple secondary outcomes, increasing the number of possible statistical comparisons.

In general, multiplicity arises when several hypotheses are tested. If each is assessed without adjustment, the chance of at least one apparently unusual result can increase across the family of tests. Methods for addressing this issue may define a hierarchy of outcomes, adjust the significance threshold, or otherwise specify which findings are confirmatory. No such approach is described in the registry record, so the reported p-values should be read as the stated individual test results, not as evidence that a family-wise error rate was controlled.

Missing-data handling is also not reported in detail. The registry record does not state how participants with incomplete follow-up, missing event information, or withdrawal were handled in the primary analysis. The analysis populations, including whether the primary result used all randomized participants or a defined safety population, are not reported in the registry record. Without those details, it is not possible to assess the possible influence of incomplete observation or exclusions.

The registry does report group denominators for the displayed outcomes, but these alone do not establish how the denominators were chosen or whether all randomized participants contributed. The record also does not describe imputation, sensitivity analyses, interim analyses, or the original analysis plan. These gaps limit a full audit of the statistical approach; they should be treated as reporting limitations rather than evidence that a particular method was or was not used.

16. 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 (1.6%), pneumonia (0.5%), bronchopneumonia (0.3%), dengue fever (0.3%), gastroenteritis (0.3%).

The separate adverse-event summary reports serious adverse events in 16 of 871 participants in the IC51 0.25 mL group, 7 of 540 in the IC51 0.5 mL group, 10 of 394 in the Havrix 720 group, and 1 of 64 in the Prevnar group. The registry also lists serious-event terms and their reported percentages, including febrile convulsion at 1.6%, pneumonia at 0.5%, bronchopneumonia at 0.3%, dengue fever at 0.3%, gastroenteritis at 0.3%, and familial periodic paralysis at 0.3%.

These are counts of participants with serious adverse events, not proof that vaccination caused the events. The registry record does not report deaths in these groups, and the displayed figures do not establish comparative causation. Group sizes differ, so raw counts alone should not be compared without considering the number at risk and the endpoint definition. The adverse-event summary also distinguishes serious events from other adverse events; the latter should not be conflated with the primary composite endpoint of serious and medically attended events through Day 56.

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

The posted results describe how frequently certain safety outcomes were recorded in the study groups and report the sponsor's statistical comparisons within age strata. The rates and confidence intervals give a descriptive account of event occurrence, while the sponsor's Fisher exact tests provide the registry's inferential comparisons. The results are specific to the enrolled pediatric study population, the vaccine schedules, the active comparators, and the follow-up intervals used.

These results do not establish that a particular adverse event was caused by a vaccine. An event occurring after vaccination is not necessarily an event caused by vaccination, and the registry record does not provide a causal adjudication for the listed events. The results also do not establish that the groups are equivalent simply because a comparison has a larger p-value. Demonstrating equivalence or non-inferiority would require a design and analysis addressing those questions, which are not reported as the primary objective.

The primary outcome concerns safety, not prevention of Japanese encephalitis. Although the study also lists antibody titers and seroconversion as secondary outcomes, the record summarized in these results does not provide enough numerical information to draw a complete conclusion about immunogenicity. Nor can the findings be generalized automatically to other age groups, populations, or dosing schedules not described in the registry.

Finally, interpretation is bounded by the reporting detail. The registry record does not report the original sample-size justification, detailed missing-data procedures, analysis populations, or multiplicity handling. Those omissions make it harder to assess how sensitive the reported conclusions may be to analytic choices. The sponsor's reported analysis remains the primary source for the trial's inferential result, while the recalculations are descriptive and unadjusted checks.

18. Why This Trial Matters Statistically

This trial illustrates why the comparator and population definition are central to interpreting a clinical result. The safety comparisons were age-stratified, with Prevnar for participants younger than 1 year and Havrix 720 for participants aged 1 year and above. Because the control vaccine changes with age, one overall comparison would obscure the structure of the study and could mix populations with different event frequencies.

It also illustrates the distinction between a rate and an inference. Arm-level percentages show observed event frequencies, while a test evaluates a specified contrast under statistical assumptions. A p-value alone does not describe the size or precision of a difference. Confidence intervals provide information about uncertainty, but arm-specific intervals are not the same as an interval for the between-group contrast.

The discrepancy between the sponsor's reported analyses and unadjusted recalculations is a practical reminder that summary data may not reproduce an analysis using the intended strata and groups. Recalculation can be informative as a check, but it cannot replace a reported analysis when the contrasts differ. The registry also demonstrates how missing details about multiplicity, missing data, and analysis populations constrain independent assessment. These are general statistical considerations, applied to the information recorded for this study.

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 gives limited detail about the original statistical design. The sample-size justification, allocation concealment, full analysis plan, interim analyses, missing-data procedures, and analysis populations are not reported. It is therefore not possible to verify how the study's planned design assumptions relate to the posted results or how incomplete follow-up was handled.

The open-label design means masking was not used. The registry record does not describe whether outcome assessment was independently adjudicated or whether specific procedures were used to reduce the influence of awareness of treatment assignment. Such details matter for safety reporting, especially for outcomes involving medical attendance or event classification.

Age determines the active comparator, so the primary results are comparisons within distinct age groups rather than a single common-control comparison. Group sizes differ, particularly in the younger stratum, and the corresponding confidence intervals are less precise. The sponsor's reported results and the unadjusted recalculations also differ for the older-group comparison; the record does not explain the reason, and the sponsor's own analysis takes precedence.

The record lists several secondary outcomes, but does not provide a complete set of numerical results for all of them in the posted material. It also does not report a multiplicity strategy. These limitations restrict the ability to synthesize all outcomes or to treat secondary findings as confirmatory. Finally, the safety endpoint is bounded by the specified follow-up period; it cannot describe events outside that period.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Immunogenicity of the Japanese Encephalitis Vaccine IC51 (IXIARO®) in a Pediatric Population — NCT01041573.
• Registry record last updated 2021-07-27; status last verified 2021-07.
• Results first posted 2014-02-27.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes NCT01041573 as a completed, randomized, open-label, active-controlled, parallel Phase 3 study of IC51 Japanese encephalitis vaccine in a pediatric population from endemic regions. Enrollment was 1869. The primary outcome was the rate of participants with serious and medically attended adverse events through Day 56, compared with age-specific active controls.

The sponsor reported Fisher exact tests for the two age-stratified comparisons. The primary arm-level rates and confidence intervals describe the observed safety outcomes, while the listed secondary outcomes include immunogenicity and additional safety measures. The record does not report several details needed for a full statistical audit, including original sample-size justification, missing-data handling, analysis populations, and multiplicity procedures. Unadjusted recalculations are distinct from the sponsor's analysis; where they differ, the sponsor's own analysis takes precedence.