VAXCHORA Pediatric Study to Assess Safety and Immunogenicity: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for VAXCHORA Pediatric Study to Assess Safety and Immunogenicity (NCT03220737), a randomized phase 4 study. The primary outcome is Cohort 1 (12-17 Yrs) Primary Endpoint - Seroconversion of Serum Vibriocidal Antibody Against V. Cholerae.

2. Clinical Question

The endpoint is an immune-response measure, not a count of cholera cases. The registry describes the study’s goals as evaluating safety and immunogenicity in children. It does not report a clinical-disease endpoint in the primary outcome. The interpretation therefore concerns the measured antibody response at the specified visit and does not establish how often participants would develop cholera or how well the vaccine prevents disease in this study population.

3. Trial Design

This is a Phase 4 study with randomized allocation and quadruple masking. The registry labels its model “sequential,” but it does not report the operational details of that model, the sequence of cohort enrollment, or how the masking was implemented. The study status is completed. The record gives a start date of 2017-07-21 and a primary completion date of 2019-09-10.

The study enrolled children in three age cohorts: 12 to 17 years, 6 to 11 years, and 2 to 5 years. Within each cohort, the active group received VAXCHORA and the placebo group received 0.9% saline. Doses were given orally on Day 1. The described study visits for these cohorts were on Days 11, 29, 91, and 181. Participants in the adolescent active group who continued in the long-term follow-up substudy also had visits on Days 365, 547, and 730.

The registry reports total enrollment of 550. That total is not the denominator for every outcome: the primary endpoint analysis is in the Immunogenicity Evaluable Population and includes 157 active-group participants and 23 placebo-group participants. The safety counts use different group denominators. These differences reflect distinct reported analysis sets or outcome populations; the registry record does not explain all participant-flow details or why the endpoint denominators differ from the safety denominators.

A historical adult bridging population is also described. It consists of historical VAXCHORA data from another study and is identified as a comparator bridging population for Day 11 seroconversion. It is not a concurrent randomized pediatric group, so it should not be treated as equivalent to the pediatric placebo comparator. The registry record does not report the full protocol, the rationale for each cohort size, or further details of the sequential model.

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: This study included healthy volunteers (2 - 17 years) who were not previously immunized against cholera. A total of 574 subjects were screened, of which 24 were screen failures. A total of 550 subjects randomized, of which 471 received study treatment and 506 and 62 completed the main and sub studies, respectively. Recruitment July 2017-July 2018. The historical control subjects are not included in the protocol enrollment number for PXVX-VC-200-006. They are solely a comparator population.

Only the first 6 of 7 groups are shown.

Main Study (Day 1 - 181)

Reasons for not completing this period:

Placebo Crossover (Day 181-365)

Reasons for not completing this period:

Long-term Follow-up (Day 365-730)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Immunogenicity Evaluable Population (IEP)

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.

Only the first 6 of 8 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Cohort 1 (12-17 Yrs) Primary Endpoint - Seroconversion of Serum Vibriocidal Antibody Against V. Cholerae, measured over Day 11.

The primary endpoint is the proportion of adolescents in the Immunogenicity Evaluable Population who achieved seroconversion of serum vibriocidal antibody against the classical Inaba biotype of V. cholerae at Day 11. Seroconversion is defined as a fourfold or greater rise over the Day 1 baseline titer after one dose of VAXCHORA. The endpoint is assessed as a percentage of participants, with a 98.3% confidence interval specified in the registry outcome description.

Serum vibriocidal antibody is an immunologic measure. A defined rise from an individual’s baseline provides a way to classify whether that participant met the study’s prespecified immune-response criterion at a particular visit. Reporting a proportion makes the result interpretable as the share of the analyzed group meeting that criterion. Comparing the active and placebo groups helps place the observed response in the context of the randomized study design.

This type of endpoint is used to assess immunogenicity, rather than directly measuring clinical illness. A participant meeting the seroconversion definition is counted as meeting the antibody-response criterion; this does not mean the participant was observed to be protected from disease. The endpoint also captures response at Day 11 and does not by itself describe how long that response persists. Later outcomes address other visits, but each is a separate time-specific measure. The registry record does not report a primary clinical cholera outcome.

7. Results Posted in the Registry

• Cohort 1 (Active, 12-17 Yrs): 99.4% (156/157) versus 0.0% (0/23) on control; risk difference 99.4 percentage points (95% CI 98.1 to 100.6); 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.

Cohort 1 (12 to <18 Years) - Seroconversion of SVA - Day 91

• 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:
  • Cohort 1 (Active, 12-17 Yrs): 85.9% (134/156) versus 0.0% (0/23) on control; risk difference 85.9 percentage points (95% CI 80.4 to 91.4); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Cohort 1 (Active, 12-17 Yrs) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Cohort 1 (12 to <18 Years) - Seroconversion of SVA - Day 181

• 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:
  • Cohort 1 (Active, 12-17 Yrs): 73.7% (115/156) versus 0.0% (0/23) on control; risk difference 73.7 percentage points (95% CI 66.8 to 80.6); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Cohort 1 (Active, 12-17 Yrs) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Cohort 2 (6 to <12 Years) - Seroconversion of SVA - Day 29

• 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:
  • Cohort 2 (Active, 6 - 11 Yrs): 94.9% (131/138) versus 4.3% (1/23) on control; risk difference 90.6 percentage points (95% CI 81.5 to 99.7), risk ratio 21.83 (3.21–148.52); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Cohort 2 (Active, 6 - 11 Yrs) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes continue the immunogenicity assessment across later visits and age cohorts. In adolescents, the registry includes seroconversion outcomes at later follow-up visits, while younger cohorts have a Day 29 outcome. The numerical results available in the record show that antibody responses were also observed beyond the primary Day 11 assessment and in a younger age cohort. These secondary endpoints extend the immune-response picture, but they are not interchangeable with the primary endpoint: each uses its own age group and follow-up time.

The secondary pattern is broadly consistent with the primary result in that the active groups show higher reported seroconversion proportions than their placebo groups for the posted comparisons. The immune-response proportions are not identical across follow-up visits, which is expected to matter when outcomes are measured at different times. Those measurements address persistence or response at specific visits; they do not transform the primary antibody endpoint into a clinical disease outcome. Numerical results for other listed secondary time points are not reported in the registry record.

The secondary comparisons are exploratory in interpretation unless the analysis plan establishes otherwise. Each additional endpoint creates another opportunity to observe a small p-value by chance when many hypotheses are tested. A p-value described as unadjusted does not account for that multiplicity. The registry record does not report a multiplicity adjustment, a hierarchy of secondary hypotheses, or a rule for controlling the overall error rate. Consequently, the secondary results are useful for describing the pattern across visits and cohorts, but they carry less confirmatory weight than a single prespecified primary analysis.

Differences in participant numbers and outcome populations also matter. The primary analysis uses the Immunogenicity Evaluable Population, and secondary analyses can have different denominators at different visits. The record does not provide enough participant-flow detail to determine all reasons for those changes. The secondary outcomes should therefore be read as visit-specific summaries, not as a complete longitudinal account for every participant enrolled.

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

• Cohort 1 (12 to <18 Years) - Seroconversion of SVA - Day 29
• Cohort 1 (12 to <18 Years) - Seroconversion of SVA - Day 91
• Cohort 1 (12 to <18 Years) - Seroconversion of SVA - Day 181
• Cohort 1 (12 to <18 Years) - Seroconversion of SVA - Day 365
• Cohort 1 (12 to <18 Years) - Seroconversion of SVA - Day 547
• Cohort 1 (12 to <18 Years) - Seroconversion of SVA - Day 730
• Cohort 2 (6 to <12 Years) - Seroconversion of SVA - Day 29
• Cohort 3 (2 to <6 Years) - Seroconversion of SVA - Day 29

9. Statistical Interpretation

10. Statistical Methods Explained

A binary percentage outcome records whether each participant met a criterion or did not. For this endpoint, the criterion is a fourfold or greater rise in serum vibriocidal antibody from the Day 1 baseline by Day 11. The reported percentage is the proportion of the analyzed group meeting that definition. It is not a measure of the magnitude of antibody rise beyond the threshold, and it is not a clinical event rate.

A confidence interval gives a range of values compatible with the observed data under the method used to construct it. It conveys sampling uncertainty: a narrow interval indicates greater precision, while a wide interval indicates greater uncertainty. It is not a range containing a stated fraction of individual participants, and it does not account automatically for possible bias, missing data, or limitations in the analysis design. The primary endpoint description specifies a 98.3% confidence interval, while the posted group estimates display intervals of 95.4% to 99.9% for active and 0.0% to 14.3% for placebo. These are distinct reported interval details and should not be assumed to use identical methods.

The risk difference is the active-group proportion minus the comparator-group proportion. It describes an absolute contrast, unlike a ratio measure. The registry’s recalculated risk difference is 0.994, with an interval from 0.981 to 1.006. A conventional normal-based interval for a difference can extend beyond the mathematically possible range for a probability difference. Such an endpoint is a property of the interval approximation, not a claim that a probability difference greater than 1.0 can occur. The registry also reports an unadjusted p-value of <0.001 for this recalculation. A p-value measures how incompatible the observed data are with a specified null model, under its assumptions; it is not the probability that the null hypothesis is true, nor does it measure clinical importance.

The registry describes the primary endpoint as a proportion and labels the sponsor-reported analysis as non-inferiority. That analysis reports a proportion of 0.985 and a lower confidence bound of 0.7 at 98.3% confidence; no upper bound is reported. Non-inferiority inference depends on a prespecified margin and analysis plan. Those details are not reported in the registry record, so the margin, the precise decision rule, and the sponsor’s full method cannot be reconstructed from the posted values alone.

For secondary binary outcomes, the registry reports Fisher Exact tests for the adolescent Day 91 and Day 181 comparisons and the younger-cohort Day 29 comparison. Fisher’s Exact test evaluates group differences using the observed counts and is commonly useful when event counts are small. The reported sponsor p-values for these secondary outcomes are < 0.001. The recalculated comparisons also carry unadjusted p-values of <0.001. “Unadjusted” means these values do not reflect a correction for the number of outcome comparisons. The registry record does not report whether a multiplicity strategy was specified elsewhere.

Over-dispersion is a general concern when outcomes vary more than a model assumes. For a binary outcome, the main issue is not a count model with an estimated dispersion parameter; rather, interpretation depends on the appropriateness of the binomial sampling assumptions, the analysis population, and the interval and test methods. More broadly, extra variability can make standard errors too small if a model fails to account for it. The registry record does not report a model-based adjustment for over-dispersion or enough detail to assess such a procedure.

The sample-size illustrations associated with the Cohort 2 Day 29 comparison are planning calculations based on the observed effect, equal allocation, a two-sided significance level of 0.05, and a normal approximation. They are not the study’s observed power and do not establish the sample-size rationale used to design the trial. Planning for 100% of the observed effect gives 4 participants per arm for 80% power and 4 participants per arm for 90% power. Planning for 75% of the observed effect gives 7 participants per arm for 80% power and 9 participants per arm for 90% power. Planning for 50% of the observed effect gives 14 participants per arm for 80% power and 19 participants per arm for 90% power. These are illustrations of how required group sizes depend on the assumed effect; they do not describe actual enrollment or prove that a future study with those group sizes would attain the stated power.

The primary endpoint analysis is identified as using the Immunogenicity Evaluable Population. The registry record does not report the complete inclusion rules for that population, how missing Day 11 observations were handled, or whether sensitivity analyses were performed. Those details can influence the interpretation of a proportion and its uncertainty, particularly if participants with missing measurements differ from those with observed measurements. No additional analytic assumptions should be inferred from the posted summary statistics.

11. Confidence Intervals and Precision

Precision is reflected in the width of an estimate’s confidence interval. For Day 11 seroconversion among adolescents, the active-group estimate is 99.4%, with a 95.4% to 99.9% confidence interval. The placebo estimate is 0.0%, with a 0.0% to 14.3% confidence interval. The active-group interval is concentrated near the top of the proportion scale. The placebo interval is broader, consistent with greater uncertainty around an estimate based on 23 participants rather than 157.

A zero observed proportion does not demonstrate that the true response probability is exactly zero. The placebo interval reaches as high as 14.3%, indicating that values above zero remain compatible with the estimate under the reported interval method. Likewise, a high active-group estimate is not a guarantee that every participant in a wider population would meet the response criterion. The intervals describe uncertainty in group-level estimates, not certainty about individual outcomes.

The recalculated risk-difference interval is 0.981 to 1.006. Its upper endpoint is beyond the feasible limit for a probability difference. This is a reminder that interval construction can affect the displayed bounds; the point estimate and interval should be interpreted as a statistical contrast, not as a literal range of possible probabilities. The registry record also reports the endpoint’s 98.3% confidence interval convention and a sponsor analysis with a lower bound of 0.7, but it does not report an upper bound for that sponsor result.

Confidence intervals do not capture every source of uncertainty. They do not resolve uncertainty about analysis-population definitions, missing measurements, the generalizability of the enrolled groups, or how well the registry’s posted analysis reflects the complete statistical plan. Precision should therefore be judged alongside the population and outcome definition, not from interval width alone.

12. Analyses Reported by the Sponsor

The registry reports a sponsor analysis for the primary endpoint as a non-inferiority analysis in the active adolescent group. It gives a proportion of 0.985 and a lower confidence bound of 0.7 at 98.3% confidence; no upper bound or p-value is reported for that analysis. The record does not identify the non-inferiority margin, the detailed method, or the full decision rule. Without those details, the reported result cannot be independently reconstructed as a complete non-inferiority assessment.

The recalculation is a different summary: it compares the observed active and placebo proportions as an unadjusted risk difference, with an unadjusted p-value of <0.001. It is not a replacement for the sponsor’s analysis and does not answer the same stated non-inferiority question. The sponsor’s proportion estimate of 0.985 also differs from the posted active-arm percentage of 99.4%, reflecting that the quantities are reported in different analyses. The registry does not explain the distinction in enough detail to attribute the difference to a particular analysis set or method.

There is no flagged discrepancy between the recalculation and the reported analysis. Even so, the sponsor’s analysis is the relevant primary analysis reported by the registry, while the recalculation is a simple, unadjusted comparison from posted summary statistics. It should be treated as a supplementary description rather than as a substitute for the sponsor’s prespecified analysis. The missing protocol and analysis-plan details limit further reconciliation.

13. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several statistical hypotheses are assessed. Even if each test uses the same nominal threshold, the chance of at least one false-positive result can increase as the number of tests grows. This is a general statistical issue; it does not show that a particular finding is false. The registry lists multiple immune-response outcomes across age cohorts and follow-up visits and reports several secondary comparisons. The record does not report whether the investigators controlled the family-wise error rate, used a hierarchical testing sequence, or designated some secondary analyses as exploratory.

The primary endpoint is clearly described as the adolescent Day 11 seroconversion proportion, but the full statistical analysis plan is not reported in the registry record. The record does not state the sample-size justification, the non-inferiority margin, whether interim analyses were planned or conducted, or the complete set of analysis rules. Those details should not be inferred from the number of enrolled participants or from the posted p-values.

Missing data and analysis populations are also important. The primary outcome uses the Immunogenicity Evaluable Population, but eligibility criteria for that population and the handling of missing Day 11 titers are not reported. The registry does not state whether missing results were excluded, imputed, or examined in sensitivity analyses. If the chance of having an observed antibody measurement is related to response, excluding missing observations could affect the estimate. The posted summary does not establish whether that occurred.

The total enrollment is 550, while the primary endpoint denominators are 157 active and 23 placebo participants. Safety denominators differ again. The record does not provide a full accounting that reconciles these numbers, nor does it describe all reasons for exclusion or loss to follow-up. This limits assessment of how representative the analyzed participants are of everyone enrolled. These reporting gaps do not erase the observed group contrast, but they constrain conclusions about the analysis plan, missingness, and the robustness of secondary findings.

14. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: asthma (3.8%), pneumonia (3.8%), lower limb fracture (0.6%), intentional overdose (0.6%), convulsion (0.6%).

The registry reports serious adverse events for the study groups, with zero deaths in every listed group. In the adolescent active group, 4 of 165 participants were reported with a serious adverse event; the adolescent placebo group had 0 of 24. The younger active groups had 0 of 157 and 0 of 146, while the corresponding placebo groups had 0 of 25 and 1 of 26. These are the registry’s reported counts, not estimates of comparative risk adjusted for exposure or follow-up.

Asthma and pneumonia are the listed leading serious-event terms, each reported as 3.8%; lower limb fracture, intentional overdose, convulsion, and local swelling are each reported as 0.6%. The registry excerpt does not give enough context to determine the denominator or timing associated with those term percentages. The counts for other adverse events are also reported separately from serious events; for example, the adolescent active group has 116 participants with other adverse events and the placebo group has 13.

Serious adverse event counts are descriptive. They do not by themselves establish whether an event was caused by the intervention, and small or unequal group sizes limit simple comparisons. The registry record does not provide event-level narratives or causal assessments in the details. These figures should be interpreted as recorded safety summaries, not as a complete evaluation of safety or a basis for individual treatment decisions.

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

The central statistical finding is that the adolescent active group had a high Day 11 seroconversion proportion under the study’s definition, while the placebo group had no observed seroconversions in the analyzed participants. The reported group percentages, confidence intervals, and unadjusted comparison describe a pronounced difference in this measured antibody response. They support a conclusion about the observed immunogenicity endpoint in the analyzed cohort.

The finding does not mean that the study directly measured prevention of cholera. The primary endpoint is a laboratory antibody criterion, not clinical disease incidence. It also does not establish the magnitude of protection for any individual participant or guarantee that the response persists indefinitely. Later immune-response assessments provide additional time-specific information, but they do not answer every question about duration or clinical effectiveness.

The result is limited to the adolescent primary analysis and its Immunogenicity Evaluable Population. The study also included younger cohorts, but their outcomes are separate analyses and should not be treated as if they were part of the adolescent primary estimate. The historical adult bridging population is not a concurrent pediatric placebo group. Generalization beyond the studied groups and settings requires caution, particularly because the registry does not report complete details on participant flow, missing data, or the statistical analysis plan.

The confidence intervals communicate sampling uncertainty, but they do not account for every possible source of bias or uncertainty. The smaller placebo denominator yields a wider interval, and the zero observed response should not be interpreted as certainty that the population response is zero. The recalculated p-value also does not measure the size or importance of an effect and does not replace the sponsor’s reported non-inferiority analysis.

Overall, the posted statistics describe a strong difference in the prespecified Day 11 immune-response measure in adolescents. They do not, by themselves, establish clinical protection, resolve all safety questions, or substitute for details absent from the registry record.

16. Why This Trial Matters Statistically

This study is statistically informative because it separates an immunologic outcome from a clinical outcome. The primary endpoint is a clearly defined binary response based on change from an individual baseline. That makes the response proportion straightforward to summarize, while also requiring careful explanation: meeting a seroconversion threshold is not the same as observing disease prevention.

The randomized placebo comparison provides a concurrent reference for the adolescent cohort. The striking difference between the reported group proportions is easy to see, but the confidence intervals show why group size still matters. The active estimate is based on 157 participants, whereas the placebo estimate is based on 23. A zero count in a smaller group remains uncertain, which is why the placebo interval extends above zero.

The study also illustrates the distinction between a sponsor-reported analysis and a recalculation from summary statistics. The sponsor’s reported primary analysis is labeled non-inferiority, while the recalculation estimates an unadjusted risk difference. These analyses answer different statistical questions and cannot be treated as interchangeable. Understanding the estimand and analysis method is as important as reading the numerical result.

Finally, the multiple ages and follow-up visits demonstrate why secondary results require context. Each time point addresses a different question, and unadjusted testing across several outcomes provides less confirmatory evidence than a prespecified primary analysis. The registry’s limited reporting of multiplicity, missing-data handling, and the sample-size rationale is therefore important. The posted result can be interpreted clearly at the endpoint level, while broader claims require information that the registry record does not report.

17. 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.

Several limitations are specific to the registry information and study structure. The primary immunogenicity result is for adolescents, whereas the study enrolled children across three age cohorts. The adolescent estimate should not be assumed to apply identically to children aged 6 to 11 years or 2 to 5 years. The secondary outcomes provide separate age- and time-specific summaries, not a single combined estimate across all children.

The primary analysis denominators are notably different from total enrollment and from the safety denominators. Although the primary analysis is identified as using the Immunogenicity Evaluable Population, the registry does not report a complete participant-flow account or all rules for entry into that population. Reasons for missing or excluded measurements and the handling of missing data are not reported in the registry record. This makes it difficult to assess how the analyzed set relates to all randomized participants.

The sponsor-reported primary result is labeled non-inferiority, but the registry does not report the non-inferiority margin, the complete analysis method, or an upper confidence bound. The recalculated risk difference is informative as a simple unadjusted contrast, but it does not reconstruct that sponsor analysis. The registry record also does not report the protocol’s sample-size justification or whether interim analyses occurred.

The outcome is an antibody response rather than observed cholera disease. The record therefore cannot answer a clinical disease-prevention question from this primary endpoint alone. The historical adult bridging population is not a concurrent randomized pediatric group, and its details should not be used as a substitute for the randomized pediatric comparison. Finally, safety counts are descriptive, with limited event context in the reported summary; they do not establish causality or provide a full safety assessment.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: VAXCHORA Pediatric Study to Assess Safety and Immunogenicity — NCT03220737.
• Registry record last updated 2023-06-28; status last verified 2023-06.
• Results first posted 2020-11-19.
• 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.

21. Record Summary

The completed Phase 4 study evaluated VAXCHORA safety and immunogenicity in children aged 2 to <18 years. It used randomized allocation and quadruple masking, with vaccine and 0.9% saline groups across three age cohorts. Total enrollment was 550.

The primary outcome was adolescent Day 11 seroconversion in the Immunogenicity Evaluable Population, defined as a fourfold or greater rise in serum vibriocidal antibody from Day 1. The active-group proportion was 99.4% (95.4% to 99.9%), compared with 0.0% (0.0% to 14.3%) for placebo. The registry also reports a sponsor non-inferiority analysis, but its margin and full method are not reported.

Secondary immune-response outcomes cover additional visits and younger cohorts. Safety summaries include serious adverse event counts and zero deaths across the listed groups. Missing-data handling, multiplicity procedures, the sample-size rationale, and other statistical-plan details are not reported in the registry record.