MVA-BN-RSV Vaccine Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for MVA-BN-RSV Vaccine Trial (NCT05238025), a randomized phase 3 study. The primary outcome is Occurrence of PCR Confirmed RSV-associated LRTD With at Least 3 Symptoms.

2. Clinical Question

The endpoint concerns an illness episode, not simply a positive RSV test. The registry definition requires clinical evidence of at least 1 sign or symptom of acute respiratory disease, at least 3 LRTD signs or symptoms, confirmation and documentation by a medical professional, and RSV confirmation by polymerase chain reaction (PCR). The definition specifies onset at least 14 days after vaccination. The displayed timeframe says follow-up ran to the end of one RSV season, up to a maximum of 11 months. Elsewhere, the endpoint definition describes the season as extending up to 12 months after vaccination; this difference in wording is not resolved in the registry record.

The main comparison therefore asks whether the number of participants meeting this clinical and laboratory definition differed between the vaccine and placebo groups during the stated observation period. It does not, by itself, address every RSV illness, every respiratory symptom, or outcomes beyond the defined season. The record also lists secondary questions about RSV-associated acute respiratory disease, complications, hospitalization, severe LRTD, and adverse events. Those outcomes add context, but they do not replace the primary question.

3. Trial Design

The registry describes a randomized, double-blind, phase 3 trial with a parallel-group design. Participants were assigned to a single dose of MVA-BN-RSV or a single dose of placebo, both given by intramuscular injection. The masking field is recorded as quadruple. The registry does not explain which groups were included in that masking designation or how masking was maintained.

The record lists enrollment of 20419 and identifies Bavarian Nordic as the sponsor. It records a start date of 2022-04-19 and a primary completion date of 2023-06-29. The status is listed as terminated. The reason for termination and the timing or circumstances of that decision are not reported in the registry record, so the status alone should not be taken to explain the posted results.

The primary outcome is reported for the Full Analysis Set. The registry defines this as randomized participants who received study vaccine, with analysis according to randomized treatment assignment. The outcome arm counts use denominators of 9160.0 for MVA-BN-RSV and 9188.0 for placebo. These outcome denominators differ from the enrollment figure; the registry record does not explain the relationship between enrollment and the analysis denominators in the material.

The trial compares one assigned intervention with one placebo comparator in parallel groups. This structure makes the between-group contrast central to interpretation: the event counts in each arm are informative, but the contrast and its uncertainty are more useful than either count alone. The registry does not report the original sample-size justification, detailed conduct of follow-up, or the reason for termination. It also does not describe the allocation sequence or operational procedures for masking. These details should not be inferred from the design labels.

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: Full Analysis Set i.e., all participants who were randomized to any treatment arm and received study vaccine (MVA-BN-RSV or placebo). Participants were analyzed based on the treatment to which they were randomized. Participants who received multiple doses of study vaccine ("multiple enrollers") were included once in this analysis set with group allocation based on their first randomization and with data censored from the time of second randomization.

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: Full Analysis Set i.e., all participants who were randomized to any treatment arm and received study vaccine (MVA-BN-RSV or placebo). Participants were analyzed based on the treatment to which they were randomized. Participants who received multiple doses of study vaccine ("multiple enrollers") were included once in this analysis set with group allocation based on their first randomization.

6. Primary Endpoint

The registry lists the primary outcome as Occurrence of PCR Confirmed RSV-associated LRTD With at Least 3 Symptoms, measured over From 14 days post-vaccination up to the end of one RSV season, up to a maximum of 11 months.

The primary endpoint is the occurrence of PCR-confirmed RSV-associated LRTD with at least 3 symptoms. It counts participants who met the case definition during follow-up; it is not a count of symptoms, a measure of symptom severity across all participants, or a time-to-event measure. The case definition combines clinical findings with laboratory confirmation. A participant needed at least 1 sign or symptom of acute respiratory disease and at least 3 LRTD signs or symptoms, with onset at least 14 days after vaccination, clinical confirmation and documentation, and RSV confirmation by PCR.

This kind of endpoint is used to focus the comparison on clinically defined lower respiratory illness associated with RSV, rather than infection or a nonspecific respiratory complaint alone. Requiring PCR confirmation supports attribution to RSV, while requiring multiple LRTD symptoms makes the event definition more specific to lower respiratory disease. Those requirements also mean the endpoint captures only events that meet the full definition and are identified during the observation period.

The registry reports 12.0 participants with the endpoint among 9160.0 in the MVA-BN-RSV group and 21.0 among 9188.0 in the placebo group. The endpoint timeframe is stated as beginning 14 days after vaccination and continuing through one RSV season, up to a maximum of 11 months. The fuller definition elsewhere mentions up to 12 months after vaccination, a discrepancy in wording that should be kept in view when describing the measurement window.

7. Results Posted in the Registry

• MVA-BN-RSV: 0.1% (12/9160) versus 0.2% (21/9188) on control; risk difference -0.1 percentage points (95% CI -0.2 to 0.0), risk ratio 0.57 (0.28–1.16); unadjusted two-proportion z-test p = 0.119.

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.

Occurrence of PCR Confirmed RSV-associated ARD

• 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:
  • MVA-BN-RSV: 0.5% (42/9160) versus 0.9% (82/9188) on control; risk difference -0.4 percentage points (95% CI -0.7 to -0.2), risk ratio 0.51 (0.35–0.74); 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 MVA-BN-RSV than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Occurrence of Complications Related to PCR-confirmed RSV Disease

• 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:
  • MVA-BN-RSV: 0.0% (0/9160) versus 0.0% (1/9188) on control; risk difference -0.0 percentage points (95% CI -0.0 to 0.0); unadjusted two-proportion z-test p = 0.318.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between MVA-BN-RSV and the control. The interval gives the range of effects that remain compatible with the data.

Occurrence of Hospitalization Due to Confirmed RSV Disease or Due to Any Complication Related to RSV-confirmed Respiratory Disease

• 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:
  • MVA-BN-RSV: 0.0% (0/9160) versus 0.0% (1/9188) on control; risk difference -0.0 percentage points (95% CI -0.0 to 0.0); unadjusted two-proportion z-test p = 0.318.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between MVA-BN-RSV and the control. The interval gives the range of effects that remain compatible with the data.

The secondary endpoints provide additional descriptions of RSV illness, related complications and hospitalization, alongside safety outcomes. Across the efficacy-related secondary results summarized in the registry, the acute respiratory disease endpoint has a more informative event count than the complication and hospitalization outcomes. The latter outcomes have very few observed events. This means the secondary set is not uniformly precise: results for more frequent illness outcomes can be estimated more informatively than results based on only a small number of events.

The RSV-associated ARD result is directionally consistent with the primary count comparison, but it is a different endpoint with a broader clinical definition. Its sponsor-reported vaccine-efficacy interval is above zero, and the recalculated unadjusted p-value is <0.001. In contrast, the posted counts for complications and hospitalization are sparse and their recalculated p-values are 0.318. These differences do not contradict the primary result: they reflect distinct event definitions and, especially for rare outcomes, different amounts of information. The table presents the endpoint-specific data and should be consulted rather than treating all secondary measures as one combined result.

Unadjusted secondary results carry less weight for confirmatory interpretation when multiple outcomes or analyses are considered. The chance of at least one apparently unusual result can increase across a collection of tests. Whether that issue was addressed through a prespecified hierarchy, family-wise procedure, or another approach is not reported in the registry record. The secondary p-values should therefore be read as descriptive evidence, not as a set of independently definitive findings.

The registry lists other secondary outcomes covering serious adverse events, grade 3 or higher adverse events, solicited local and systemic adverse events, and severe PCR-confirmed RSV-associated LRTD. The overall pattern should be interpreted outcome by outcome, with attention to the underlying event counts and intervals where posted. These outcomes broaden the scope of what the trial recorded, but they do not alter the primary endpoint definition or settle uncertainty in the sponsor’s primary analysis.

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

• Occurrence of PCR Confirmed RSV-associated ARD
• Occurrence of Complications Related to PCR-confirmed RSV Disease
• Occurrence of Hospitalization Due to Confirmed RSV Disease or Due to Any Complication Related to RSV-confirmed Respiratory Disease
• Occurrence of Severe PCR Confirmed RSV-associated LRTD
• Number of Participants With Serious Adverse Events
• Number of Participants With Grade 3 or Higher Adverse Events
• Number of Participants With Solicited Local Adverse Events
• Number of Participants With Solicited Systemic Adverse Events

9. Statistical Interpretation

10. Statistical Methods Explained

What is being compared?

The primary outcome is binary at the participant level: each participant either met the stated case definition during the observation window or did not. The registry reports the number meeting the definition and the number analyzed in each group. For such an outcome, a natural descriptive comparison is the risk, meaning the proportion of participants in each group who experienced the event. A risk difference subtracts the comparator risk from the intervention risk. A negative risk difference in this setup means the observed event proportion is lower in the MVA-BN-RSV group, while a positive value means it is higher. The recalculated comparison is an unadjusted contrast based on the posted summary counts.

Other possible measures describe relative rather than absolute differences. A risk ratio compares the two risks by division; an odds ratio compares the odds of the event. These measures answer related but distinct questions, and they need not have the same numerical value. The registry also reports the sponsor’s primary analysis as vaccine efficacy, with a confidence interval. The record does not give enough detail to reconstruct the sponsor’s full statistical procedure, so the posted efficacy estimate should be described as reported rather than reverse-engineered.

What does a confidence interval communicate?

General statistical explanation: a confidence interval describes uncertainty around an estimate under the assumptions of the method used to calculate it. A narrower interval indicates greater precision; a wider interval indicates less precision. An interval that includes the null value for the measure does not rule out no difference under that analysis. For a risk difference, the null is zero; for a ratio measure, it is one. For the sponsor’s vaccine-efficacy scale, the reported interval extends below and above zero, which shows substantial uncertainty in the direction and size of the estimate.

The interval is not a guarantee that the true effect lies within its endpoints, nor does it show the probability that a particular treatment effect is true. It is a repeated-sampling concept: in general, intervals constructed using the same method would cover the underlying parameter at their stated rate across repeated studies, if the model assumptions hold. The 95% label in the sponsor analysis identifies the confidence level attached to that interval; it does not eliminate uncertainty in this one trial.

How should the p-value be read?

The recalculated primary p-value is 0.119. General statistical explanation: a p-value describes how incompatible the observed data, or data more extreme, would be with a specified null model, assuming that model and the analysis assumptions are appropriate. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The registry labels this recalculation unadjusted. It should not be mistaken for the sponsor’s p-value, because the sponsor’s analysis has no p-value posted in this record.

For the secondary RSV-associated ARD comparison, the recalculated p-value is <0.001. The other listed secondary comparisons have recalculated p-values of 0.318. These are unadjusted values. Without a stated multiplicity procedure, they should not be interpreted as if they were adjusted for the full set of outcomes and analyses. The registry record does not state whether a prespecified hierarchy or other multiplicity strategy was used.

Why do rare events matter?

General statistical explanation: when an outcome is uncommon, the estimate can depend heavily on a small number of events. This can make uncertainty intervals wide even when the groups have large denominators. It can also make relative measures sensitive to very small changes in event counts. A non-significant result is not proof of equivalence or absence of an effect; it may reflect imprecision, a small underlying difference, or both. Conversely, a small p-value for a secondary outcome does not by itself establish the importance of that result, especially where many outcomes are examined.

For the primary endpoint, there were 12.0 and 21.0 observed events across the two groups. The sponsor’s interval is broad and crosses zero on the vaccine-efficacy scale. That combination argues for describing the result with both the point estimate and uncertainty, not by focusing on a single number. The displayed arm counts are still useful for understanding how sparse the outcome was, but counts alone do not establish the comparative effect.

What is recalculated and what is reported?

The recalculated figures are simple, unadjusted analyses derived from posted summary statistics. They are not a substitute for an individual-participant analysis and cannot reproduce methods that depend on detailed participant-level data, covariate adjustment, censoring, or other unreported design features. The registry provides the sponsor-reported efficacy estimate for the primary outcome and for RSV-associated ARD, but does not name the method used to produce them. Other analysis-method details are not reported in the registry record.

The record identifies the primary population as the Full Analysis Set and says participants were analyzed according to randomized treatment assignment after receiving study vaccine. Its description of the population is incomplete in the record text. No additional assumptions about exclusions, missing observations, or how incomplete follow-up was handled should be added. Those omissions matter because interpretation depends not only on the event definition, but also on which participants and observations contributed to each analysis.

11. Confidence Intervals and Precision

Precision is best judged from the interval around an estimate, not from the point estimate alone. The sponsor’s primary analysis reports vaccine efficacy of 42.9 with a 95% confidence interval from -16.1 to 71.9. This interval spans negative and positive values, so the estimated direction is uncertain. It is also broad, meaning the posted analysis does not pin down a narrow range of plausible effects. The sponsor analysis does not include a p-value in the registry record.

The recalculated primary risk-difference analysis reports p = 0.119. The posted recalculation interval for the risk difference also crosses zero, consistent with uncertainty about whether the event proportions differ. Because its endpoints are recorded with more than three decimal places, they are not reproduced. The sponsor’s reported vaccine-efficacy interval and the recalculated risk-difference interval use different effect scales; they should not be compared as if their endpoints measured the same quantity.

There were 12.0 primary events in the MVA-BN-RSV arm and 21.0 in the placebo arm. These counts are sparse relative to the denominators, which helps explain why the estimate should not be read as a precise measurement of the underlying effect. Larger denominators do not guarantee a precise estimate when the event itself is uncommon.

General statistical explanation: an interval crossing the null does not demonstrate that the groups are identical. It indicates that the data and method do not distinguish the observed estimate from the null with the interval’s stated confidence level. Precision is also different from importance: a narrow interval can precisely estimate a small effect, while a wide interval can leave substantial uncertainty about effects of different sizes. Here, the sponsor’s interval leaves meaningful uncertainty about both direction and magnitude.

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 table is a planning illustration based on the observed effect, not a record of the trial’s original design calculation. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect targeted in each row is the stated fraction of the observed effect. For these binary outcomes, the figures are participants per arm, not total events. The note about total events applies to time-to-event tables; the outcomes are not time-to-event outcomes.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under the listed assumptions, if that effect were the true one and the assumptions held. The 90% power column gives the corresponding planning count for a higher chance of detection. These are planning quantities, not guarantees of a study result. The trial’s own original assumptions and sample-size justification are not reported in the registry record.

Rows that plan for 100% of the observed effect use the observed effect as the target; rows for 75% and 50% plan for smaller effects. Smaller effects are harder to distinguish from random variation, so they require more participants per arm for the same planned power. The table therefore illustrates how the required sample size changes when the assumed effect is made more conservative. It should not be read as evidence that any particular future study will achieve its target effect or as a reconstruction of the enrollment decision for this trial.

This is not observed power. It is a prospective planning illustration computed from the observed effect and the stated assumptions. The table and its associated curve can help readers see the relationship between the assumed effect size, planned power, and participant count, but they do not add information to the trial’s observed outcome or resolve uncertainty in the posted estimates.

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 = 0.002; treatment proportion p₁ = 0.001; average p̄ = 0.002.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.0599 = 0.1174.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.0599 = 0.0504.
4. n = (0.1174 + 0.0504)² / (-0.0010)² = 29,599.8, rounded up to 29,600 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 <- 0.00228558989986939                          # control proportion
p1 <- 0.00131004366812227                          # 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(5238025)
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 = 29,600 (80% power), 39,626 (90% power)
 75% of observed effect: n per arm = 56,186 (80% power), 75,216 (90% power)
 50% of observed effect: n per arm = 134,433 (80% power), 179,967 (90% power)
power.prop.test: 29599.8 
Simulated power at n = 29,600 per arm: 0.802 (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 the sponsor’s primary analysis as vaccine efficacy of 42.9, with a 95% confidence interval from -16.1 to 71.9. It does not give a p-value for that analysis or identify the method used to calculate it in the material. The sponsor’s own result is the reported trial analysis and should take precedence over a simple recalculation from summary counts when describing the sponsor’s conclusion.

The recalculation uses the posted event counts and denominators to form an unadjusted risk-difference comparison. Its p-value is 0.119, and its interval crosses zero. This re-analysis is useful as a transparent check based on the summary numbers, but it does not reproduce unknown features of the sponsor’s analysis. The sponsor’s vaccine-efficacy measure and the recalculated risk difference are also expressed on different scales. Their numerical values cannot be directly compared or treated as competing estimates of one identical quantity.

There is no flagged discrepancy between the sponsor report and recalculation in the registry material. The two analyses nevertheless serve different roles: the registry’s sponsor analysis is the primary reported estimate, while the recalculation offers an unadjusted comparison from the posted arm summaries. Neither removes the uncertainty shown by the broad sponsor interval.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 15 outcome measures and 3 analyses. Several secondary endpoints are reported in addition to the primary outcome, and recalculated comparisons are available for a subset of them. When many outcomes or statistical tests are examined, the chance of finding at least one apparently strong result by chance can rise. Statistical methods for multiplicity can control that risk, but the appropriate interpretation depends on which outcomes were prespecified, how they were ordered, and what adjustment strategy was planned.

The registry record does not report whether the trial used a multiplicity adjustment, a hierarchical testing procedure, or another strategy to control false-positive risk across outcomes. It also does not report a detailed statistical analysis plan in the material. The p-values shown for recalculated comparisons are unadjusted. They should therefore not be read as though they automatically account for the full collection of endpoint and analysis opportunities.

The record identifies the primary population as the Full Analysis Set: participants randomized to any treatment arm who received study vaccine, analyzed according to randomized assignment. However, the population description ends mid-sentence. Further details about the treatment of participants who received multiple doses are not complete in this discussion. The record does not explain how missing endpoint assessments, incomplete follow-up, or other missing data were handled. It also does not state whether the sponsor’s analysis used imputation, censoring, sensitivity analyses, or another strategy; these should not be inferred.

Randomization supports a comparison between groups, but the analysis population and missing-data handling still matter. If participants are not observed for the full outcome window, the available records may not capture every event that would have occurred under complete follow-up. The posted information does not permit an assessment of the extent or direction of any such issue. The termination status also makes it important not to assume that all planned analyses or follow-up were completed; the reason and analytic consequences of termination are not reported in the registry record.

These reporting gaps do not invalidate the posted results, but they limit how completely readers can assess their confirmatory status and robustness. The most defensible reading distinguishes the registry’s sponsor-reported primary analysis from unadjusted recalculations and secondary comparisons, and recognizes that multiplicity, missing-data handling, and additional analysis details remain unknown.

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 0.5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (0.4%), osteoarthritis (0.3%), atrial fibrillation (0.2%), chronic obstructive pulmonary disease (0.2%), acute myocardial infarction (0.2%).

The registry reports serious adverse events among 517 of 9389 participants at risk in the MVA-BN-RSV group and 422 of 9191 participants at risk in the placebo group. It also lists 41 deaths in the MVA-BN-RSV group and 34 in the placebo group. These are descriptive counts and denominators; the record excerpt does not provide a comparative statistical analysis for these figures. They should not be read as establishing that an event was caused by vaccination or as a direct estimate of comparative risk without considering follow-up and analysis details.

The most frequent serious-event terms listed include pneumonia at 0.4%, osteoarthritis at 0.3%, atrial fibrillation at 0.2%, chronic obstructive pulmonary disease at 0.2%, acute myocardial infarction at 0.2%, and cerebrovascular accident at 0.2%. These terms are reported as percentages, but the summary does not give event counts for each term or explain whether categories can overlap. The full safety interpretation also depends on the observation period, coding approach, and rules for classifying events, which are not described in the summarized record.

Serious adverse events are distinct from other adverse-event categories, including solicited local or systemic events and events graded by severity. The registry lists several such secondary safety outcomes, but their detailed results are not reproduced. The figures above are best treated as a descriptive account of the posted serious-event data, not as proof of causation or as a complete safety comparison.

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

The primary endpoint counts were lower in the MVA-BN-RSV arm than in the placebo arm during the stated follow-up window. The sponsor’s reported vaccine-efficacy estimate was 42.9, but its 95% confidence interval ranged from -16.1 to 71.9. That interval includes values on either side of zero and is broad, so the posted primary analysis leaves substantial uncertainty about the direction and size of the underlying comparison. The unadjusted recalculation likewise does not provide strong evidence of a primary difference, with p = 0.119.

This result does not show that the groups were identical. It also does not establish a precise benefit or harm. A failure to distinguish the estimate from the null is not equivalent to proof of no effect, particularly when the endpoint is uncommon and the observed event counts are small. The results describe what was observed in this trial and the uncertainty around the comparison; they do not establish what would occur in every population or setting.

The endpoint is limited to PCR-confirmed RSV-associated LRTD meeting a specific symptom definition and occurring in the stated seasonal window. It does not cover every RSV infection, every respiratory illness, longer-term outcomes, or outcomes that the registry did not report. The acute respiratory disease secondary result relates to a broader endpoint and should not be substituted for the primary endpoint. Rare complication and hospitalization outcomes are especially difficult to interpret precisely from the very small event counts posted.

The safety information is also descriptive. Counts of serious adverse events and deaths do not, by themselves, establish cause or a comparative safety effect. The registry’s status is terminated, but its reason for termination is not reported. Without that explanation, it is not appropriate to attribute termination to efficacy, safety, feasibility, or any other factor. The overall meaning is therefore bounded: these are randomized trial results with a primary estimate that remains imprecise, alongside secondary and safety information that must be interpreted according to their definitions and limitations.

18. Why This Trial Matters Statistically

This trial illustrates why the number of participants alone does not determine how precisely an uncommon clinical outcome can be estimated. The analysis denominators are large, but the primary endpoint occurred in only 12.0 and 21.0 participants in the two arms. With few events, the estimated difference is sensitive to the observed event count and the uncertainty can remain substantial. Readers need the interval and the event counts as well as the point estimate.

It also shows why the reported analysis and a simple recalculation should be kept distinct. The sponsor reports vaccine efficacy, while the summary-statistic recalculation reports an unadjusted risk difference and p-value. Each describes the comparison on a different scale and may depend on different analytical details. Transparent recalculation can help readers understand the posted summaries, but it cannot replace the sponsor’s analysis or recreate details absent from the registry record.

The secondary outcomes demonstrate another general issue: evidence can vary across endpoints because definitions and event frequencies differ. A result for a broader respiratory-disease endpoint does not answer precisely the same question as the primary LRTD endpoint. Outcomes with very few events offer limited precision, while unadjusted testing across several secondary outcomes raises questions about multiplicity.

Finally, design and reporting details affect interpretation. The record identifies randomization, masking, and the analysis population, but leaves the original sample-size rationale, multiplicity strategy, missing-data methods, and reason for termination unreported. Statistical interpretation is strongest when it states both what the numerical results show and what the registry does not allow readers to conclude.

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.

Several limitations specific to this record constrain interpretation. First, the primary outcome description gives two different upper limits for the observation period: the timeframe field says up to 11 months, while the fuller definition says up to 12 months after vaccination. The registry record does not reconcile these descriptions. Because the event count depends on the observation window, this wording difference is relevant when describing the endpoint.

Second, the primary analysis population description is incomplete: the text ends after referring to participants who received multiple doses. The record identifies the Full Analysis Set and randomized assignment, but does not provide the rest of that explanation. The enrollment figure and the primary outcome denominators also differ, and the record does not explain that difference. No further account of exclusions or analysis-set construction should be inferred.

Third, the status is terminated, but the reason for termination is not reported in the registry record. The record excerpt also does not provide the original sample-size justification, detailed statistical analysis plan, multiplicity procedure, missing-data strategy, or method used for the sponsor’s vaccine-efficacy analysis. These omissions limit independent assessment of the planned analysis and whether all intended follow-up and analyses were completed.

Finally, the primary endpoint was uncommon, and the sponsor’s interval is broad. Secondary outcomes based on very few events are less informative, while multiple unadjusted secondary comparisons merit caution. The posted summaries support description of the recorded results, but do not support conclusions about unreported outcomes, the reason for trial termination, or the effect of any analysis choices that are not documented.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: MVA-BN-RSV Vaccine Trial — NCT05238025.
• Registry record last updated 2024-10-31; status last verified 2024-10.
• Results first posted 2024-10-31.
• 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

This registry record describes a randomized, double-blind, phase 3, parallel-group trial comparing a single intramuscular dose of MVA-BN-RSV with a single intramuscular placebo dose in adults aged 60 years and older. It lists enrollment of 20419, sponsor Bavarian Nordic, and status terminated.

The primary endpoint was PCR-confirmed RSV-associated LRTD with at least 3 symptoms. The posted counts were 12.0 among 9160.0 participants in the MVA-BN-RSV group and 21.0 among 9188.0 in the placebo group. The sponsor reported vaccine efficacy of 42.9 with a 95% confidence interval from -16.1 to 71.9. An unadjusted recalculation gives p = 0.119. The interval indicates substantial uncertainty in the primary comparison.

The record also lists secondary respiratory and safety outcomes. Important details, including the termination reason, original sample-size justification, multiplicity approach, missing-data handling, and complete analysis-population description, are not reported in the registry record.