Study of a Single Intramuscular Dose of Nirsevimab in the Prevention of Hospitalizations Due to Respiratory Syncytial Virus (RSV) Infection in Healthy Term and Preterm Infants During the First Year of Life: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of a Single Intramuscular Dose of Nirsevimab in the Prevention of Hospitalizations Due to Respiratory Syncytial Virus (RSV) Infection in Healthy Term and Preterm Infants During the First Year of Life (NCT05437510), a randomized phase 3 study. The primary outcome is Number of Participants With Respiratory Syncytial Virus (RSV) Lower Respiratory Tract Infection (LRTI) Hospitalization Through the Respiratory Syncytial Virus Season.

2. Clinical Question

The clinical question focuses on hospitalization associated with confirmed RSV infection, rather than infection alone. The registry defines lower respiratory tract infection using findings that include rhonchi, rales, crackles, or wheeze; an increased respiratory rate at rest; and hypoxemia. Hospitalization was defined as the treating physician’s decision to admit the participant to inpatient care. The RSV season was described as the period of increased RSV infection.

The endpoint timeframe began at dosing or randomization on Day 1 and continued through approximately 7 months. The comparison therefore concerns events within the stated seasonal follow-up window, not every RSV-related event over the full follow-up period. The trial also collected other outcomes, including very severe RSV lower respiratory tract infection, all-cause lower respiratory tract infection hospitalization, and adverse events.

3. Trial Design

This was a Phase IIIb, randomized, parallel-group, open-label study. Participants were assigned to nirsevimab or no intervention; masking was listed as none. The registry reports enrollment of 8057 participants. The nirsevimab group received one intramuscular injection at Day 01, while the comparison group received no RSV preventive intervention.

The primary endpoint analysis used the All Randomized Set, defined in the registry as all participants randomly assigned to either group. The primary outcome was assessed from dosing or randomization through approximately 7 months, corresponding to the RSV season. The study was completed. Its recorded start date was 2022-08-08 and its primary completion date was 2024-03-27.

Follow-up included one in-person dosing or randomization visit and monthly electronic safety contacts through the first 6 months after dosing or randomization for all participants. A telephone follow-up was planned at 12 months. The registry also describes 18-month and 24-month telephone follow-up for UK participants who reconsented; the 24-month call was the final telephone call for that group. The 12-month call was the final follow-up telephone call for France, Germany, and UK participants who did not reconsent.

Because the study was open-label, participants and study staff were not masked to assignment. Whether outcome assessors or event adjudicators were separately masked is not reported in the registry record. Details of allocation concealment and the full statistical analysis plan are also not reported in the registry record.

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: Total 8057 participants were enrolled and randomized in 1:1 ratio to nirsevimab or no intervention group between 08 August 2022 to 28 February 2023. Participants were followed up for safety for 12-months (366 days) (for France, Germany, and UK non-reconsented participants) and for 24 months (731 days) (for UK participants who consented to take part into study extension \[UK reconsented participants\]). As pre-specified in protocol and SAP, results are presented by treatment group.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The All Randomized Set consisted of all participants randomly assigned to either the nirsevimab group or the no intervention group.

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 All Randomized Set consisted of all participants randomly assigned to either the nirsevimab group or the no intervention group.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Respiratory Syncytial Virus (RSV) Lower Respiratory Tract Infection (LRTI) Hospitalization Through the Respiratory Syncytial Virus Season, measured over From dosing/randomization (Day 1) up to approximately 7 months.

The primary endpoint counted participants with RSV lower respiratory tract infection hospitalization through the RSV season. It is a binary participant-level outcome: each participant either had a qualifying hospitalization during the specified timeframe or did not. The outcome is not a count of the number of separate hospitalizations per participant.

The registry defines lower respiratory tract infection using specified respiratory findings, including rhonchi, rales, crackles, or wheeze, increased respiratory rate at rest, and hypoxemia. RSV infection had to be confirmed. Hospitalization was based on the treating physician’s decision to admit the participant to inpatient care. The endpoint timeframe ran from dosing or randomization on Day 1 to approximately 7 months.

This kind of endpoint is used to focus on a clinically consequential event rather than a laboratory finding or infection without hospitalization. Comparing participant counts between randomized groups gives a direct account of how often the recorded event occurred in each group during the stated follow-up. The endpoint does not, by itself, describe symptom severity among participants who were not hospitalized, the duration of hospitalization, or all RSV infections. Those questions require other outcomes or data not reported in the registry record.

7. Results Posted in the Registry

• No Intervention: 1.6% (64/4019) versus 0.3% (11/4038) on control; risk difference 1.3 percentage points (95% CI 0.9 to 1.7), risk ratio 5.85 (3.09–11.07); 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.

Number of Participants With Very Severe Respiratory Syncytial Virus Lower Respiratory Tract Infection Through the Respiratory Syncytial Virus Season

• 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:
  • No Intervention: 0.5% (21/4019) versus 0.1% (5/4038) on control; risk difference 0.4 percentage points (95% CI 0.2 to 0.6), risk ratio 4.22 (1.59–11.18); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for No Intervention than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Hospitalization for All-Cause Lower Respiratory Tract Infection From Days 181 to 366 Post-dosing/Randomization

• 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:
  • No Intervention: 1.4% (55/3881) versus 1.7% (68/3956) on control; risk difference -0.3 percentage points (95% CI -0.9 to 0.2), risk ratio 0.82 (0.58–1.17); unadjusted two-proportion z-test p = 0.283.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between No Intervention and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Respiratory Syncytial Virus Lower Respiratory Tract Infection Hospitalization From Days 366 to 731 Post-dosing/Randomization (for United Kingdom Reconsented Participants)

• 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:
  • No Intervention: 0.2% (2/1062) versus 0.6% (7/1132) on control; risk difference -0.4 percentage points (95% CI -1.0 to 0.1), risk ratio 0.30 (0.06–1.46); unadjusted two-proportion z-test p = 0.115.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between No Intervention and the control. The interval gives the range of effects that remain compatible with the data.

The detailed secondary results cover different event definitions and follow-up windows, so they do not all estimate one common effect. The reported very severe RSV lower respiratory tract infection outcome follows the same general direction as the primary RSV hospitalization comparison. By contrast, the later all-cause lower respiratory tract infection hospitalization result and the extended UK reconsented-participant RSV hospitalization result have different observed directions and intervals that include no difference. These outcomes should not be collapsed into a single overall secondary conclusion.

The broader secondary outcome list includes RSV outcomes, all-cause lower respiratory tract infection hospitalization, and treatment-emergent adverse events. The registry lists 17 posted secondary outcomes, but the results described in detail in this record concern selected outcomes and periods. Results for other secondary endpoints are not reported in the registry record, so their direction or precision should not be inferred from the named outcomes.

The primary outcome is the prespecified central comparison in the record and has a sponsor-reported analysis. Secondary outcomes can help characterize whether patterns extend to other definitions or timeframes, but each involves its own event count, denominator, and uncertainty. In general, testing many outcomes increases the chance that some results appear notable by chance. Because an adjustment for multiple comparisons is not reported in the registry record, unadjusted secondary p-values carry less confirmatory weight than the primary analysis and should be interpreted cautiously rather than as separate proof of effects.

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

• Number of Participants With Very Severe Respiratory Syncytial Virus Lower Respiratory Tract Infection Through the Respiratory Syncytial Virus Season
• Number of Participants With Respiratory Syncytial Virus Lower Respiratory Tract Infection Hospitalization Through the Respiratory Syncytial Virus Season in Each Country
• Number of Participants With Hospitalization for All-Cause Lower Respiratory Tract Infection Through the Respiratory Syncytial Virus Season
• Number of Participants With Respiratory Syncytial Virus Lower Respiratory Tract Infection Hospitalization Through 151 Days Post-dosing/Randomization
• Number of Participants With Very Severe Respiratory Syncytial Virus Lower Respiratory Tract Infection Through 151 Days Post-dosing/Randomization
• Number of Participants With Hospitalization for All-Cause Lower Respiratory Tract Infection Through 151 Days Post-dosing/Randomization
• Number of Participants With Immediate Treatment-Emergent Adverse Events (TEAEs)
• Number of Participants With Non-Serious Treatment-Emergent Adverse Events

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because it records whether each participant experienced at least one qualifying RSV lower respiratory tract infection hospitalization during the specified period. For this type of endpoint, a basic comparison can describe the number of events and the number of participants in each group, then estimate a difference between the groups’ observed risks. The posted group risks are 0.003 for nirsevimab and 0.016 for no intervention. The recalculated risk difference is 0.013, defined in the direction of no intervention minus nirsevimab.

In general, an absolute risk difference expresses a contrast on the same scale as the event probability. It can be easier to interpret as a change in event frequency than a relative measure, but it depends on the event rates in the groups and the follow-up period. A risk ratio instead compares one group’s risk with the other group’s risk. The posted risk ratio is 5.846, with a 95% confidence interval from 3.088 to 11.07, for no intervention relative to nirsevimab. The posted odds ratio is 5.924, with a 95% confidence interval from 3.12 to 11.25. Risk ratios and odds ratios answer related but different questions, and neither replaces the absolute risk difference.

The registry’s sponsor-reported primary efficacy analysis used an exact method based on the binomial distribution. It reports efficacy of 84.04, a 95% confidence interval from 69.493 to 92.411, and p < 0.001. The registry labels the analysis as superiority. The specific formula used to construct the posted recalculated risk-difference interval is not reported in the registry record. It is therefore important not to assume that the sponsor’s exact binomial analysis and the unadjusted recalculation use the same estimand or interval method.

In general, a confidence interval conveys uncertainty about an estimated quantity: narrower intervals indicate greater precision, while wider intervals indicate less precision. A p-value describes how unusual results at least as incompatible with a specified null hypothesis would be under that hypothesis and the model assumptions. It is not the probability that the null hypothesis is true, nor a measure of the size or clinical importance of an effect. For the primary outcome, the posted unadjusted p-value is <0.001; the sponsor’s analysis has its own p-value, p < 0.001.

The trial randomized participants to parallel groups and used an All Randomized Set for the primary analysis, according to the registry’s description. Randomization supports a comparison of groups by assigned intervention, but it does not eliminate uncertainty or guarantee that every relevant aspect of conduct and measurement was identical. The study was open-label, and the registry does not report whether outcome assessors were masked, how missing primary outcome data were handled, or the detailed procedures used to confirm and adjudicate endpoint events. Those details matter because hospitalization decisions and the recording of clinical findings can involve judgment.

The secondary outcomes include other binary participant counts, such as very severe RSV lower respiratory tract infection and hospitalizations for all-cause lower respiratory tract infection. Their effect estimates and p-values are separate analyses, not additional tests of the exact same endpoint. In general, results across different outcomes and time windows may vary because the event definitions, follow-up periods, and participant sets differ. The registry does not report an adjustment for multiple comparisons in the record. Unadjusted secondary p-values should consequently be treated as exploratory signals rather than as a set of independent confirmatory conclusions.

For binary outcomes, over-dispersion is not the central issue in the way it can be for count models that allow variance to exceed the mean. The central statistical choices concern the event definition, group risks, contrast measure, interval construction, analysis population, and treatment of missing outcomes. The full protocol and detailed analysis plan, including any further sensitivity analyses or interim analyses, are not reported in the registry record.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.013, with a 95% confidence interval from 0.009 to 0.017. This interval lies above zero, so the posted interval is compatible with a positive difference in the stated direction: higher observed risk in the no-intervention group than in the nirsevimab group. The interval also shows that the precise size of the risk difference is uncertain; it should not be reduced to a single point estimate.

In general, a 95% confidence interval is a range produced by a method that, under repeated use and its assumptions, would cover the target quantity at the stated frequency. It is not a range containing 95% of individual outcomes, and it does not mean that there is a 95% probability that the fixed true value is inside this particular interval. The interval’s width reflects uncertainty in the estimate, but its interpretation also depends on the outcome definition, follow-up, and analysis method.

The sponsor-reported efficacy estimate has a separate 95% confidence interval, from 69.493 to 92.411. That interval belongs to the sponsor’s exact binomial analysis and should not be read as an interval for the risk difference. For the secondary outcomes, some posted recalculated intervals include zero and others do not; the interval and estimand need to be considered for each outcome. The registry does not report a multiplicity adjustment for these secondary comparisons.

Precision is also affected by the number of observed events, not only by the total number randomized. The primary groups had 11 and 64 recorded events. The trial’s overall enrollment therefore does not mean that every outcome estimate is equally precise, particularly for less frequent outcomes or analyses restricted to a subgroup or later period.

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 illustrations use the observed effect as a starting point and show planning scenarios for detecting the full observed effect, 75% of the observed effect, or 50% of the observed effect. For this binary primary outcome, the figures are participants per arm, not total events. The assumptions listed for the illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the target effect is the stated fraction of the observed effect.

The 80% power column gives the planned participants per arm under which the specified effect would be detected in 80% of repeated studies if the assumptions and effect were correct. The 90% power column uses a higher probability of detection and therefore generally calls for a larger planned group size. Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants per arm.

These figures are planning illustrations based on the observed effect, not a reconstruction of the trial’s original sample-size calculation. The original trial design assumptions and sample-size justification are not reported in the registry record. These calculations are not observed power; they do not describe the probability that the completed trial’s observed result was true or establish the probability that another study will reproduce it. They are conditional planning quantities under the listed assumptions, and they may be sensitive to the effect size used as the planning target.

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 = 0.003; treatment proportion p₁ = 0.016; average p̄ = 0.009.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1359 = 0.2664.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1356 = 0.1141.
4. n = (0.2664 + 0.1141)² / (0.0132)² = 831.0, rounded up to 832 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 <- 0.00272412085190688                          # control proportion
p1 <- 0.0159243592933566                          # 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(5437510)
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 = 832 (80% power), 1,112 (90% power)
 75% of observed effect: n per arm = 1,219 (80% power), 1,631 (90% power)
 50% of observed effect: n per arm = 2,157 (80% power), 2,887 (90% power)
power.prop.test: 831 
Simulated power at n = 832 per arm: 0.838 (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 a sponsor efficacy analysis for the primary endpoint using an exact method based on the binomial distribution. Its estimate is 84.04, with a 95% confidence interval from 69.493 to 92.411 and p < 0.001. The registry identifies this as a superiority analysis. The unadjusted recalculation gives the group risks, a risk difference of 0.013 with a 95% confidence interval from 0.009 to 0.017, and p < 0.001.

These are different summaries of the randomized comparison. The sponsor’s efficacy measure and the recalculated absolute risk difference have different scales and may use different statistical constructions. The registry record does not give enough detail to treat them as identical estimands. Both are reported as evidence of a group contrast for the primary outcome, while the sponsor’s analysis remains the trial’s own reported analysis and the recalculation is a simple unadjusted comparison of posted summary data.

The registry record does not identify a discrepancy between these analyses. The recalculation is useful for interpreting the absolute event-risk contrast, but it does not replace the sponsor’s stated analysis or its method.

15. Multiplicity, Missing Data and Analysis Populations

The registry record describes the primary outcome and multiple secondary outcomes, but a multiplicity-control procedure is not reported in the registry record. Multiplicity refers to the statistical issue created when several hypotheses are tested: even if none of the tested effects is real, the chance of at least one small p-value can increase as the number of tests grows. Without a stated adjustment or testing hierarchy, secondary p-values should not be interpreted as if they came from one isolated, prespecified test.

The record identifies the primary analysis population as the All Randomized Set, consisting of all participants randomly assigned to either group. It does not give a detailed account of how missing primary endpoint information was handled, whether participants with incomplete follow-up were included in every analysis, or whether sensitivity analyses were used to examine missingness. The amount and pattern of missing outcome data are not reported in the registry record.

Follow-up contacts and telephone calls are described, including different later follow-up schedules for some participants by country and reconsent status. However, the registry record does not report the resulting completeness of follow-up for each outcome or how the differing follow-up windows were incorporated into every analysis. The primary endpoint timeframe is through approximately 7 months; later outcomes use their stated periods and may have different analysis populations.

The record gives the exact binomial method for the sponsor’s primary efficacy analysis, but the full statistical analysis plan, interim analyses, detailed missing-data assumptions, and any multiplicity strategy are not reported in the registry record. These gaps limit independent assessment of whether all analytic choices and outcome reporting followed a prespecified plan.

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: gastroenteritis (0.3%), seizure (0.3%), viral infection (0.3%), pyrexia (0.3%), febrile convulsion (0.2%).

For serious adverse events, the registry reports 262 affected participants among 4016 at risk in the nirsevimab group and 222 among 4018 at risk in the no-intervention group. These are participant counts with a serious adverse event, not counts of all serious-event episodes. The registry also reports 1 death in the nirsevimab group and 0 in the no-intervention group.

The listed leading serious adverse event terms include gastroenteritis, seizure, viral infection, and pyrexia, each reported as 0.3%, and febrile convulsion and pyelonephritis, each reported as 0.2%. These term frequencies describe recorded events; they do not establish that the events were caused by the assigned intervention. The death counts likewise do not indicate cause or treatment relationship in the information reported.

Safety comparisons should be read with the at-risk denominators and the study’s follow-up and reporting definitions in mind. The registry record does not provide a causal assessment of each event or a detailed account of how serious adverse events were adjudicated.

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

The primary result describes fewer recorded RSV lower respiratory tract infection hospitalizations in the randomized nirsevimab group than in the no-intervention group during the stated RSV-season period. The posted group counts, risks, and confidence interval quantify that comparison. The sponsor’s exact binomial efficacy analysis also reports a superiority result for the primary endpoint. Together, these statistics describe the trial’s observed primary outcome and the uncertainty associated with its estimates.

The result does not establish that every infant would have the same outcome, that every RSV infection was prevented, or that there were no events in the nirsevimab group. It is limited to the endpoint definition, population, and follow-up period in the registry. It also does not, by itself, answer questions about all-cause respiratory illness, outcomes in a different population, or events beyond the measured timeframe.

Statistical evidence for a group difference is not the same as a complete assessment of benefit and harm. The safety counts are a separate part of the record, and the reported adverse events should not be attributed to treatment solely from their occurrence in a randomized group. The record’s open-label design and limited reporting on outcome assessment, missing data, and analytic procedures are relevant context for interpreting both efficacy and safety findings.

No medical recommendation follows from these statistics alone. Applying trial results to a particular infant or care decision requires clinical judgment and information beyond the group-level registry results.

18. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can be interpreted using both an absolute measure and a sponsor-reported efficacy analysis. The primary endpoint is a concrete participant-level event—hospitalization for RSV lower respiratory tract infection—rather than infection in general. Showing event counts alongside risks and an absolute risk difference helps readers understand the scale of the observed group contrast, while the sponsor’s exact binomial analysis provides the trial’s own reported efficacy summary.

The example also shows why uncertainty matters for infrequent outcomes. The total enrollment was 8057, but the primary event counts were 11 and 64. Precision depends on the events informing a particular outcome, not simply on the overall size of the study. A confidence interval therefore belongs with the estimate rather than being treated as an optional technical detail.

Finally, multiple outcomes and follow-up periods require careful separation. Secondary results can add context, but they do not all answer the same question, and unadjusted comparisons should not automatically be treated as confirmatory. Clear distinctions among the primary endpoint, secondary outcomes, safety counts, and the sponsor’s own analysis make the statistical evidence easier to evaluate without extending the findings beyond the registry record.

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.

The study was open-label, with no masking reported. Hospitalization is a consequential outcome, but the registry’s definition includes a treating physician’s decision to admit; whether endpoint assessors or adjudicators were masked is not reported in the registry record. This leaves uncertainty about the details of event confirmation and assessment.

The primary timeframe was through approximately 7 months, while some secondary outcomes use later periods or restricted groups. The extended UK outcome concerns participants who reconsented, so it should not be assumed to represent all randomized participants. The record also describes different follow-up arrangements by country and reconsent status.

The registry does not report the detailed statistical analysis plan, original sample-size justification, handling of missing outcome data, interim analyses, or multiplicity strategy. These omissions limit evaluation of prespecification and the robustness of analyses beyond the posted primary result. The detailed results available for secondary outcomes do not encompass every secondary outcome listed in the record.

The primary endpoint captures participants with at least one qualifying hospitalization, not the number or duration of admissions, all RSV infections, or symptom burden outside hospitalization. The estimates therefore answer a focused question and should not be generalized to unmeasured outcomes or populations without additional evidence.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of a Single Intramuscular Dose of Nirsevimab in the Prevention of Hospitalizations Due to Respiratory Syncytial Virus (RSV) Infection in Healthy Term and Preterm Infants During the First Year of Life — NCT05437510.
• Registry record last updated 2025-10-09; status last verified 2025-09.
• Results first posted 2025-04-11.
• 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

NCT05437510 is a completed, randomized, open-label Phase IIIb parallel-group study of a single intramuscular dose of nirsevimab versus no RSV preventive intervention in infants under 12 months who were not eligible to receive palivizumab. The registry reports enrollment of 8057 participants.

The primary endpoint was the number of participants hospitalized for RSV lower respiratory tract infection through the RSV season. The recorded counts were 11 in the nirsevimab group and 64 in the no-intervention group. The sponsor reported an exact binomial superiority analysis, while the posted unadjusted comparison gives a risk difference of 0.013 with a 95% confidence interval from 0.009 to 0.017.

Interpretation should account for the open-label design, endpoint timeframe, uncertainty, multiple outcomes, and details of missing-data and analysis procedures that are not reported in the registry record.