Study on an Investigational Yellow Fever Vaccine Compared With Stamaril in Adults in Europe and Asia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study on an Investigational Yellow Fever Vaccine Compared With Stamaril in Adults in Europe and Asia (NCT05011123), a randomized phase 2 study. The primary outcome is Percentage of Yellow Fever-naive Participants Who Achieved Seroconversion 28 Days Post Dose 1 Enrolled in European Union.

2. Clinical Question

3. Trial Design

This is a phase II, randomized, parallel-group, active-controlled study of an investigational yellow fever vaccine. The registry lists an enrollment of 690 and identifies the condition as Yellow Fever. The study was conducted in Europe and Asia: the primary efficacy question concerns adults in the European Union, while safety and immunogenicity in a cohort of participants of Chinese origin in Asia were also to be described. The brief summary specifies adults aged 18 years up to 60 years in Europe and says the Asian participants were of Chinese origin outside China.

Participants were assigned to receive vYF or Stamaril. The brief summary describes a 2:1 allocation and a single subcutaneous injection on Day 1. The design field identifies the study as quadruple-masked; the brief summary describes it as observer-blind. These are the registry’s descriptions, and further details about which roles were masked are not reported in the registry record. The stated study aims include non-inferiority of the immune response, assessment of immunogenicity profiles, and assessment of safety profiles.

The registry lists the study as active, not recruiting. The recorded study start is 2021-10-07, and the primary completion date is 2022-05-23. The brief summary says each participant’s participation was expected to last approximately 5 years. The vYF and Stamaril arms are each reported as receiving a single injection. Details of the original sample-size justification and the trial’s planned statistical procedures are not reported in the registry record. The results therefore need to be read as posted outcomes from this study, not as a complete account of its protocol or analysis plan.

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: A total of 690 participants were randomized in a 2:1 ratio to receive a single subcutaneous (SC) injection of either yellow fever vaccine (vYF) vaccine or Stamaril. A subset of participants enrolled in European Union (EU) and Asia at selected sites provided an additional post-vaccination blood sample on Day 11 to assess the early immune response elicited by both vaccines in terms of neutralizing antibody (Nab) titers.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The per-protocol analysis set (PPAS) was a subset of the full analysis set (FAS). The FAS included the subset of randomized participants who received at least 1 dose of the study vaccine or control vaccine and had a valid post-vaccination blood sample result. Only YF-naive participants enrolled in EU with data collected are reported.

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.

Population: The randomized population included all participants with data in the case report form (CRF).

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Yellow Fever-naive Participants Who Achieved Seroconversion 28 Days Post Dose 1 Enrolled in European Union, measured over 28 days post dose 1 (Day 29).

The primary endpoint is the percentage of yellow-fever-naive participants enrolled in the European Union who achieved seroconversion 28 days after the first dose, at Day 29. The registry defines yellow-fever-naive participants as those with no detectable yellow fever antibody titers before vaccination. Seroconversion means a 4-fold increase in neutralizing antibody titers compared with the pre-vaccination value. The titers were determined using a validated live virus microneutralization assay.

This endpoint measures an antibody response after vaccination rather than a clinical outcome such as yellow fever illness. Seroconversion is used to describe whether an individual’s measured antibody titer has risen by the prespecified amount. Reporting the percentage who meet that definition allows a comparison of the frequency of this immune response between the investigational vaccine and the active comparator. The registry’s stated objective is non-inferiority, which asks whether the response to vYF is not unacceptably worse than the response to Stamaril according to a prespecified margin. That margin is not reported in the registry record, so the posted percentages alone do not establish the formal non-inferiority criterion.

The primary results use a per-protocol analysis set, while the registry’s definition says that set is a subset of the full analysis set. The population details for the primary analysis are partly truncated in the registry record. The registry reports percentages rounded to the tenth decimal place; the displayed arm estimates and confidence intervals should therefore be read at their posted precision.

7. Results Posted in the Registry

• Stamaril 0.5 mL: 99.4% (159/160) versus 98.1% (316/322) on control; risk difference 1.2 percentage points (95% CI -0.7 to 3.2), risk ratio 1.01 (0.99–1.03); unadjusted two-proportion z-test p = 0.285.

8. Secondary Efficacy Endpoints

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

Percentage of Participants Who Achieved Seroconversion 28 Days Post Dose 1 Enrolled in European Union

• 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:
  • Stamaril 0.5 mL: 96.8% (184/190) versus 95.9% (354/369) on control; risk difference 0.9 percentage points (95% CI -2.3 to 4.1), risk ratio 1.01 (0.98–1.04); unadjusted two-proportion z-test p = 0.593.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stamaril 0.5 mL and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Solicited Injection Site Reactions

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Stamaril 0.5 mL: 21.5% (50/233) versus 33.8% (152/450) on control; risk difference -12.3 percentage points (95% CI -19.2 to -5.5), risk ratio 0.64 (0.48–0.84); 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 Stamaril 0.5 mL than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Solicited Systemic Reactions

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Stamaril 0.5 mL: 54.1% (126/233) versus 49.3% (222/450) on control; risk difference 4.7 percentage points (95% CI -3.1 to 12.6), risk ratio 1.10 (0.94–1.27); unadjusted two-proportion z-test p = 0.240.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stamaril 0.5 mL and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the study beyond the primary European Union seroconversion comparison. They include additional seroconversion summaries, seroprotection, antibody geometric mean titers and ratios, and counts of adverse events and solicited reactions. The posted secondary results span immune-response measures and short-term reactogenicity; they answer related but distinct questions and use different timeframes and analysis populations.

The secondary seroconversion result in the European Union also shows high percentages in both arms, while the comparison interval includes zero. That general pattern is consistent with the primary result’s high observed response percentages, but it does not supply the missing non-inferiority margin or independently establish the sponsor’s formal conclusion. Other secondary immune measures describe different features of the antibody response and should not be treated as direct substitutes for the primary endpoint.

Reaction outcomes contribute information about events recorded after vaccination, but they are not efficacy outcomes. Their denominators and follow-up windows differ from those for the primary antibody endpoint. Their comparisons are unadjusted in the re-calculations. The registry does not report a multiplicity adjustment, so multiple secondary comparisons should be treated as exploratory rather than as separate confirmatory tests. When many outcomes are examined, some may appear noteworthy by chance even when there is no underlying difference. In addition, the registry lists 12 secondary outcomes as posted, but the detailed results available for interpretation do not cover every outcome in the same way. Absence of a detailed result in the registry record is not evidence that no event or response occurred.

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

• Percentage of Participants Who Achieved Seroconversion 28 Days Post Dose 1 Enrolled in European Union
• Percentage of Participants Who Achieved Seroconversion Enrolled in European Union and Asia
• Percentage of Participants Who Achieved Seroprotection to Yellow Fever Virus Enrolled in European Union and Asia
• Geometric Mean Titers (GMTs) of Antibodies Against Yellow Fever Virus in Participants Enrolled in European Union and Asia
• Geometric Mean Titers Ratio (GMTRs) of Antibodies Against Yellow Fever Virus in Participants Enrolled in European Union and Asia
• Number of Participants With Unsolicited Systemic Adverse Events (AEs)
• Number of Participants With Solicited Injection Site Reactions
• Number of Participants With Solicited Systemic Reactions

9. Statistical Interpretation

10. Statistical Methods Explained

The posted statistics include arm-level percentages, 95% confidence intervals, a sponsor-reported non-inferiority comparison, and unadjusted re-calculations based on posted summary statistics. The distinction between these forms of analysis matters: they can answer related questions but do not necessarily use the same population, method, or contrast definition.

What does a percentage describe?

For a binary endpoint such as seroconversion, each participant either meets the endpoint definition or does not. The percentage summarizes the share of participants in an arm who met that definition among those included in the reported analysis. The primary results give 98.1% for vYF and 99.4% for Stamaril. The reported denominators are 322 and 160, respectively. These denominators belong to the primary per-protocol results; they should not be confused with denominators from other outcomes, whose analysis populations differ.

A percentage is a descriptive estimate for the analyzed participants. It is not a guarantee that the same percentage would occur in another group of participants, nor does it show the individual distribution of antibody titers. The endpoint’s threshold definition also matters: the summary identifies whether titers increased by the specified amount, not how far above that threshold each participant’s result was.

What does the risk difference add?

A risk difference compares the proportions with the endpoint between two arms by subtraction. Its sign depends on which arm is placed first. The unadjusted re-calculation is expressed as Stamaril relative to vYF and gives an estimate of 0.012. Its 95% confidence interval runs from -0.007 to 0.032. Because the interval includes zero, it does not rule out no difference on that comparison scale. A confidence interval that crosses zero does not demonstrate that the groups are equivalent; it indicates that the estimated difference is imprecise enough to include zero among the values compatible with the data and calculation.

The re-calculation also reports an unadjusted p-value of 0.285. A p-value describes the compatibility of the observed data with a specified no-difference model, given the assumptions of the calculation. It is not the probability that the null hypothesis is true, and it does not quantify the probability that the treatment is beneficial or harmful. The registry does not give the method used for the sponsor’s reported comparison, so the p-value from the re-calculation should not be attributed to the sponsor analysis.

How is non-inferiority different?

A non-inferiority analysis asks whether the investigational treatment’s result is no worse than the comparator by more than a prespecified margin. This is not the same as asking whether a conventional test finds a statistically significant difference. A conclusion depends on the direction of the contrast, the confidence interval, and the chosen margin. The registry labels the sponsor analysis as non-inferiority and reports a difference of -1.2 with a 95% confidence interval from -3.4 to 1.8. The non-inferiority margin and the method are not reported in the registry record. It is therefore not possible to verify the sponsor’s formal decision rule from the posted result alone.

The randomized, parallel-group design supports a between-arm comparison, while the active comparator frames the question as a comparison with Stamaril rather than with no vaccine. The registry identifies quadruple masking in the design field but calls the study observer-blind in its brief summary. Further details about masking procedures are not reported in the registry record. Randomization and masking can reduce certain sources of bias, but they do not answer questions about missing outcome data, analysis choices, or the precision of an estimate.

Why do analysis populations matter?

The registry says the primary outcome uses a per-protocol analysis set, which is a subset of the full analysis set. It describes the full analysis set as randomized participants who received at least 1 dose and had a valid post-vaccination blood sample result. A per-protocol result may differ from a result using a broader analysis set because the participants included can differ. The complete per-protocol definition is not reported in the registry record, so the criteria for inclusion in the primary analysis cannot be fully assessed.

The secondary seroconversion result has different reported denominators from the primary result. Safety outcomes also have their own denominators. These differences mean that results should be interpreted outcome by outcome rather than assuming all analyses represent the same participants. The registry does not report enough detail to determine how missing measurements were handled or whether additional analyses tested the robustness of the primary finding.

11. Confidence Intervals and Precision

The primary arm-level confidence intervals are 96.0% to 99.3% for vYF and 96.6% to 100.0% for Stamaril, each at the 95% confidence level. A confidence interval expresses uncertainty around an estimated percentage under the method used to construct it. It is not a range that guarantees the true value lies within it, nor is it a statement that an individual participant’s response falls within those limits. The intervals are relatively close to the upper boundary of the percentage scale, and the Stamaril interval reaches 100.0% as posted.

For the unadjusted between-arm comparison, the 95% confidence interval for the risk difference is -0.007 to 0.032. The interval includes zero and also allows differences in either direction. Its breadth is relevant: the point estimate alone does not convey how much uncertainty remains. The sponsor’s reported interval, -3.4 to 1.8 for the difference in percentage of participants, is a separate result and uses the sponsor’s reported scale and contrast.

Confidence intervals do not resolve the missing non-inferiority margin. A non-inferiority interpretation requires comparing the appropriate confidence bound with that prespecified margin, and the margin is not reported in the registry record. The registry also does not give the sponsor’s method, so the source of the difference between the sponsor presentation and the re-calculation cannot be fully evaluated. The posted values are rounded, which further limits any attempt to reproduce calculations from the displayed numbers. Overall, the high arm estimates are informative about the observed seroconversion percentages, while the comparison’s uncertainty and the missing decision-rule details limit conclusions about formal non-inferiority.

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 planning figures are illustrations based on the observed effect, not the original trial’s design justification. The calculation assumes a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. It considers detecting the stated fraction of the observed effect. The registry does not report the assumptions used for the trial’s original sample-size design.

The figures are participants per arm, not totals across the trial. The 80% power column describes the per-arm planning size for a design intended to have an 80% chance of detecting the specified effect under the calculation’s assumptions, if that effect is present. The 90% power column uses a higher target chance of detection and therefore generally calls for more participants per arm. These are design-planning quantities: they are not observed power.

Each planning row changes the effect size being targeted. Planning for 100% of the observed effect uses the observed effect as the target; planning for 75% or 50% of the observed effect targets smaller differences. Smaller effects are harder to distinguish from random variation and therefore need more participants. The accompanying curve should be read as illustrating that relationship, not as evidence about the probability that the trial’s result is true. The calculations are not a substitute for the trial’s prespecified design rationale, which is not reported in the registry record.

These planning calculations depend on their assumptions and on the observed effect used as the starting point. They do not establish that the trial had adequate power for its original non-inferiority objective. That assessment would require the original target difference, non-inferiority margin, allocation and analysis assumptions, and planned sample-size rationale, which are not reported in the registry record.

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 = 0.981; treatment proportion p₁ = 0.994; average p̄ = 0.988.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1568 = 0.3072.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1565 = 0.1317.
4. n = (0.3072 + 0.1317)² / (0.0124)² = 1,256.6, rounded up to 1,257 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 <- 0.981366459627329                          # control proportion
p1 <- 0.99375                          # 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(5011123)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,257 (80% power), 1,682 (90% power)
 75% of observed effect: n per arm = 2,510 (80% power), 3,359 (90% power)
 50% of observed effect: n per arm = 6,262 (80% power), 8,383 (90% power)
power.prop.test: 1256.6 
Simulated power at n = 1,257 per arm: 0.825 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s posted primary analysis is labeled NON INFERIORITY and reports a difference in percentage of participants of -1.2, with a 95% confidence interval from -3.4 to 1.8. The sponsor’s p-value is not reported in the registry record, and neither the non-inferiority margin nor the analysis method is stated. Those missing details prevent an independent check of the formal non-inferiority decision rule.

The simple re-calculation from posted summary statistics reports a risk difference of 0.012 for Stamaril relative to vYF, with a 95% confidence interval from -0.007 to 0.032 and an unadjusted p-value of 0.285. This is not the sponsor’s analysis: the contrast is presented in the opposite arm order, and the re-calculation is explicitly unadjusted. The registry does not provide enough methodological detail to establish whether differences beyond presentation, such as the analysis population or statistical method, account for the distinct estimates and intervals.

The registry record does not flag a discrepancy between the sponsor analysis and the re-calculation. The sponsor’s result should therefore be read as the reported trial analysis, while the re-calculation is a separate descriptive check rather than a replacement for it. Neither result, by itself, supplies the missing non-inferiority margin.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the trial’s statistical analysis plan adjusted for multiple comparisons. The study includes a primary seroconversion endpoint and numerous secondary immune-response and safety outcomes. Testing or interpreting many outcomes without an adjustment can increase the chance of apparently notable findings arising by chance. For this reason, unadjusted secondary comparisons should carry less evidential weight than a prespecified primary analysis, and should generally be interpreted as descriptive or exploratory unless the analysis plan indicates otherwise.

The primary analysis is described as a per-protocol analysis set, a subset of the full analysis set. The full analysis set is defined as randomized participants who received at least 1 dose of study vaccine or control vaccine and had a valid post-vaccination blood sample result. The complete per-protocol inclusion criteria are not reported in the registry record; the available primary population description is truncated. The registry also does not report the handling of missing measurements, withdrawals, protocol deviations, or participants without valid post-vaccination samples. No imputation approach or sensitivity analysis for missing outcome data is reported in the registry record.

Different outcomes have different reported denominators. The primary per-protocol seroconversion results use 322 participants in the vYF arm and 160 in the Stamaril arm; the secondary European Union seroconversion results use 369 and 190, respectively. Safety outcomes have other denominators. These are outcome-specific analysis counts, and the registry does not provide enough detail to reconcile all population differences or to determine how they arose. The original statistical analysis plan, the non-inferiority margin, and details of interim analyses are not reported in the registry record. Without those items, readers cannot fully assess the prespecified testing hierarchy or the treatment of missing data.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: covid-19 (1.3%), pyelonephritis (0.4%), acute myocardial infarction (0.4%), appendicitis (0.4%), influenza (0.4%).

The registry reports 11 participants with serious adverse events in the vYF group among 454 at risk, and 11 in the Stamaril group among 235 at risk. It reports 0 deaths in each group. The listed serious-event terms include Covid-19 at 1.3%, and Pyelonephritis, Acute Myocardial Infarction, Appendicitis, Influenza, and Tonsillitis at 0.4% each. These figures describe events recorded in the study; the registry summary does not establish that an event was caused by vaccination.

The registry also gives counts for other adverse events, but the record does not provide enough context in these fields to interpret those counts as a causal comparison. Serious adverse events are distinct from solicited injection-site reactions and solicited systemic reactions, which were collected over specified post-vaccination windows. The safety denominators differ from the primary efficacy denominators, so they should not be used interchangeably. The registry record does not report additional detail about event adjudication or causal attribution in the information used for these results.

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

The results describe antibody responses and recorded safety outcomes after a single dose of vYF or Stamaril in this phase II study. For the primary endpoint, the posted seroconversion percentages were high in both arms among yellow-fever-naive participants in the European Union per-protocol analysis set. The unadjusted re-calculation’s confidence interval includes zero, so it does not establish a clear difference between the arms on that scale. The sponsor reports a non-inferiority analysis, but the registry record does not provide the margin needed to independently assess that conclusion.

Seroconversion is an immunogenicity measure. It records whether the antibody titer met the stated increase criterion; it is not itself a direct measurement of whether a participant would develop yellow fever after exposure. The study results therefore should not be read as proof of clinical protection, and they do not establish the duration of any immune response from the reported Day 29 endpoint. Although the brief summary describes participation lasting approximately 5 years, the primary outcome assessed is at 28 days post dose 1.

The primary efficacy question is restricted to the European Union population and the per-protocol analysis. The Asian cohort was included to describe safety and immunogenicity among participants of Chinese origin, but the primary endpoint does not combine those participants with the European Union population. Secondary outcomes add information about other immune measures and reported reactions, but they have distinct definitions, timeframes, and denominators. They should not be used to extend the primary result beyond its stated population or endpoint.

Finally, the posted results do not provide the full protocol, complete analysis plan, non-inferiority margin, missing-data procedures, or multiplicity approach. These limits do not erase the observed results, but they constrain what can be concluded from the registry record. The evidence supports a description of the measured outcomes and their uncertainty, not a broader claim about comparative clinical effectiveness or safety outside the study’s recorded populations and follow-up.

18. Why This Trial Matters Statistically

This trial illustrates why a high response percentage in each arm and a formal non-inferiority conclusion are not the same thing. The primary arm estimates are 98.1% and 99.4%, but the question of non-inferiority depends on a prespecified margin and the appropriate confidence bound. The registry labels the sponsor analysis as non-inferiority, yet does not report the margin. Readers can describe the posted response percentages and intervals, but cannot reconstruct that decision rule from the registry record alone.

The record also illustrates why the analysis population matters. The primary outcome uses the per-protocol analysis set, while related immune-response outcomes and safety outcomes have different denominators. A numerical comparison is meaningful only when its endpoint, population, timepoint, and analysis method are understood. Reporting the primary endpoint for yellow-fever-naive European Union participants should not be generalized automatically to the Asian cohort or to all randomized participants.

Finally, the study offers a useful example of the difference between sponsor-reported analysis and a simple re-calculation. The two presentations do not have identical contrast conventions or documented methods, and the re-calculation is not a substitute for the sponsor’s planned analysis. Clear reporting of the non-inferiority margin, full analysis populations, missing-data handling, and multiplicity strategy would make the statistical interpretation more complete. These are important features of a trial record because they determine how confidently readers can move from observed percentages to a formal comparative conclusion.

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 leaves important protocol and analysis details unavailable. The non-inferiority margin, original sample-size justification, statistical analysis plan, analysis method for the sponsor comparison, and any interim analyses are not reported in the registry record. Without the margin, the formal non-inferiority decision cannot be independently checked from the posted confidence interval.

The primary population description is incomplete in the registry record. It identifies the per-protocol set as a subset of the full analysis set and gives a partial definition of the full analysis set, but does not provide the complete per-protocol criteria. The record also does not describe how missing post-vaccination samples, withdrawals, or protocol deviations were handled, or whether sensitivity analyses assessed their effect. This matters because different outcomes report different denominators, and the record does not fully explain the differences.

The primary outcome is an antibody-based measure at Day 29, not a clinical disease outcome. The primary question is limited to yellow-fever-naive European Union participants, so it does not directly answer the same question for the Asian cohort. The brief summary calls the study observer-blind, while the design field identifies quadruple masking; further clarification of masking roles is not reported in the registry record. The sponsor analysis and the unadjusted re-calculation are not fully comparable because the registry does not report enough method detail to explain their respective analytic choices.

Finally, the registry does not report whether multiplicity was controlled across secondary outcomes. Those results therefore provide context but may be less reliable as confirmatory evidence. Safety event counts describe events recorded in the study and do not establish causation. These limitations are specific to interpreting this record and should be kept in view alongside the posted estimates and their confidence intervals.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study on an Investigational Yellow Fever Vaccine Compared With Stamaril in Adults in Europe and Asia — NCT05011123.
• Registry record last updated 2026-06-01; status last verified 2026-05.
• Results first posted 2025-05-21.
• 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 a phase II randomized, parallel-group, active-controlled study of an investigational yellow fever vaccine compared with Stamaril in adults in Europe and Asia. The primary outcome is seroconversion 28 days after the first dose among yellow-fever-naive participants enrolled in the European Union, analyzed in a per-protocol set. The posted percentages were 98.1% for vYF and 99.4% for Stamaril.

The sponsor reports a non-inferiority analysis, but the registry record does not report the margin or the method. An unadjusted re-calculation gives a risk difference of 0.012 for Stamaril relative to vYF, with a 95% confidence interval from -0.007 to 0.032. Secondary outcomes and safety results cover additional measures but use different populations and timeframes. Important details about missing data, multiplicity, and the original sample-size rationale are not reported in the registry record.