Study to Evaluate the Efficacy and Safety of Suptavumab (REGN2222) for the Prevention of Medically Attended RSV (Respiratory Syncytial Virus) Infection in Preterm Infants: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate the Efficacy and Safety of Suptavumab (REGN2222) for the Prevention of Medically Attended RSV (Respiratory Syncytial Virus) Infection in Preterm Infants (NCT02325791), a randomized phase 3 study. The primary outcome is Part B: Percentage of Participants With Medically Attended Respiratory Syncytial Virus (RSV) Infection (Hospitalization or Outpatient Visit With Lower Respiratory Tract Infection [LRTI]) Up to Day 150.

2. Clinical Question

The clinical question concerns prevention of a specifically defined, medically attended RSV outcome rather than every RSV infection. A participant counted toward the primary endpoint had to have a positive RSV RT-PCR test and either be hospitalized for RSV infection or have an outpatient visit with RSV LRTI. The outpatient setting could include an emergency room, urgent care, or pediatric clinic visit. The LRTI definition also required reported cough or difficulty breathing and at least one specified clinical sign.

The registry reports a placebo group and two suptavumab regimens in Part B. The primary outcome percentages were 8.1% with placebo, 7.7% with one dose, and 9.3% with two doses. The study also assessed safety, pharmacokinetics, and immunogenicity, but those questions are distinct from the primary comparison of medically attended RSV infection through Day 150.

3. Trial Design

This was a Phase 3, randomized, double-blind, placebo-controlled, parallel-group study sponsored by Regeneron Pharmaceuticals. The registry lists quadruple masking. Overall enrollment was 1177 participants. The record describes the study as completed, with a start date of 2015-07-21 and a primary completion date of 2017-07-05.

The study had Part A and Part B. The listed interventions include suptavumab 30 mg/kg in Part A, and placebo matched to suptavumab, suptavumab with one dose, and suptavumab with two doses in Part B. The primary efficacy outcome is reported for Part B. Its analysis population was the full analysis set, comprising randomized participants who received any study drug and analyzed according to their randomized allocation. The primary arm counts were 383 for placebo, 385 for one dose, and 381 for two doses.

The study was conducted during RSV season, according to the brief summary, and the intended population was infants born no more than 35 weeks, 6 days gestational age, who were no more than 6 months old at enrollment in their respective geographic location. The registry record does not report the original sample-size justification, the detailed dosing schedule beyond the listed intervention labels, or the trial's full statistical analysis plan. The record identifies six outcome measures and four posted analyses. It also lists safety, serum concentration, anti-drug antibody, and additional RSV-related outcomes among the secondary measures.

Randomization helps form comparison groups, while masking is intended to reduce the influence of treatment knowledge on care, outcome assessment, and other study processes. These are general design principles; the registry record does not specify the operational details of masking or randomization beyond the listed design characteristics.

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: In Part A, 27 participants were screened, of which 23 received study drug. In Part B, out of 1,154 participants, 1,149 received first dose of study drug. Of those, 1,051 continued and received second dose 8 weeks later. Participants were randomized in 1:1:1 ratio in Part B by gestational age category \& region (North America/Rest of World).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The PK analysis set included participants who received a single dose of suptavumab and had at least 1 measurable concentration of suptavumab in serum. Here "Number Analyzed" signifies those participants who were evaluable for this outcome measure at specific time point.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Part B: Percentage of Participants With Medically Attended Respiratory Syncytial Virus (RSV) Infection (Hospitalization or Outpatient Visit With Lower Respiratory Tract Infection [LRTI]) Up to Day 150, measured over From first study drug administration up to Day 150.

The primary endpoint was the percentage of participants with a medically attended RSV infection from first study drug administration through Day 150. The definition required a positive RSV test by RT-PCR and one of two forms of medical attendance: hospitalization for RSV infection, based on the admitting physician's assessment, or an outpatient visit with RSV lower respiratory tract infection.

For an outpatient case to qualify as RSV LRTI, the record specifies a positive RSV RT-PCR test, parent or guardian report of cough or difficulty breathing, and at least one clinical sign assessed by a healthcare provider: lower chest wall indrawing, hypoxemia, or wheezing or crackles. The record defines hypoxemia as peripheral capillary oxygen saturation <95% while breathing room air. An outpatient visit could occur in an emergency room, urgent care, or pediatric clinic.

This endpoint is used to focus the efficacy question on RSV infections that led to a defined level of medical attention, rather than counting infections without those events. As a binary percentage outcome, it records whether each participant met the endpoint during the assessment period. That makes the results interpretable as the proportion with an event in each group. It does not, by itself, describe the timing of events, their duration, or their severity beyond the criteria built into the endpoint. The registry record does not report additional detail about adjudication procedures or missing endpoint data.

7. Results Posted in the Registry

• Part B: Suptavumab 30 mg/kg- 1 Dose: 7.8% (30/385) versus 8.1% (31/383) on control; risk difference -0.3 percentage points (95% CI -4.1 to 3.5), risk ratio 0.96 (0.59–1.56); unadjusted two-proportion z-test p = 0.877.
• Part B: Suptavumab 30 mg/kg - 2 Doses: 9.2% (35/381) versus 8.1% (31/383) on control; risk difference 1.1 percentage points (95% CI -2.9 to 5.1), risk ratio 1.13 (0.71–1.80); unadjusted two-proportion z-test p = 0.591.

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.

Part B: Percentage of Participants Hospitalized With Medically Attended RSV Infection or Outpatient Visit Lower Respiratory Tract Infection (LRTI) or Upper Respiratory Tract Infection (URTI) Up to Day 150

• 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:
  • Part B: Suptavumab 30 mg/kg- 1 Dose: 11.9% (46/385) versus 12.5% (48/383) on control; risk difference -0.6 percentage points (95% CI -5.2 to 4.1), risk ratio 0.95 (0.65–1.39); unadjusted two-proportion z-test p = 0.805.
  • Part B: Suptavumab 30 mg/kg - 2 Doses: 14.4% (55/381) versus 12.5% (48/383) on control; risk difference 1.9 percentage points (95% CI -2.9 to 6.7), risk ratio 1.15 (0.80–1.65); unadjusted two-proportion z-test p = 0.441.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part B: Suptavumab 30 mg/kg- 1 Dose and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part B: Suptavumab 30 mg/kg - 2 Doses and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes extend the evaluation beyond the primary endpoint. They include a broader RSV-related outcome involving hospitalization or outpatient visits for LRTI or URTI, as well as safety, serum concentration, and anti-drug antibody measures. The additional RSV outcome uses a broader clinical definition than the primary endpoint, which is restricted to medically attended RSV infection meeting the stated hospitalization or LRTI criteria.

Across the posted binary RSV comparisons, the broad pattern is that neither suptavumab regimen shows a clear separation from placebo. The secondary RSV outcome comparisons also have recalculated confidence intervals that cross no difference. This is directionally consistent with the primary result's uncertainty, rather than providing a distinct, precise signal that resolves the primary comparison. The registry lists additional secondary outcomes, but the record does not supply numerical results for all of them in the registry record described for this analysis; those outcomes cannot be characterized from the information.

Secondary results generally carry less weight than a prespecified primary result when many outcomes or comparisons are examined. General statistical principle: each additional test creates another opportunity for an apparently notable result to arise by chance, especially if results are selected for emphasis after analysis. Adjustments for multiplicity can help control that issue, but the registry record does not report whether such adjustments were planned or applied. The secondary findings should therefore be viewed as supportive or exploratory context, not as independent confirmation of a treatment effect.

The number of outcome measures and analyses in the registry is not, by itself, enough to establish how many statistical tests were planned or how the testing sequence was controlled. The full protocol and statistical analysis plan are not reported in the registry record. Any interpretation of the secondary pattern should retain that uncertainty, and should distinguish the broader RSV endpoint from the narrower primary endpoint.

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

• Part A: Percentage of Participants With Treatment-Emergent Adverse Events (TEAEs)
• Part B: Serum Concentration of Suptavumab
• Part B: Number of Participants With At Least One Positive Anti-Drug Antibody (ADA) Assay
• Part B: Percentage of Participants Hospitalized With Medically Attended RSV Infection or Outpatient Visit Lower Respiratory Tract Infection (LRTI) or Upper Respiratory Tract Infection (URTI) Up to Day 150

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the medically attended RSV infection definition during the assessment period or did not. A percentage in each group expresses how frequently the endpoint occurred in that group. A risk difference compares the event proportions by subtracting the placebo proportion from the suptavumab proportion. Negative values indicate a lower proportion in the suptavumab group under that ordering; positive values indicate a higher proportion.

What does a confidence interval describe?

A confidence interval describes the uncertainty around an estimated effect under the assumptions of the statistical method. It is not a range containing a known fixed percentage of individual participant outcomes. In repeated use of the same procedure under its assumptions, intervals constructed in this way would cover the underlying effect at the stated confidence level at the stated frequency. For the primary comparisons, the recalculated intervals include no risk difference, so the data are compatible with effects in either direction. Their width also matters: a wide interval leaves more possible effect sizes unresolved than a narrow interval.

What does the p-value add?

A p-value measures how incompatible the observed data are with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The unadjusted p-values for the recalculated primary comparisons are 0.877 and 0.591. They do not indicate strong evidence against no difference under the corresponding unadjusted tests. Interpretation still depends on the estimate and its interval, the endpoint definition, the population analyzed, and the analysis plan.

How do the recalculated and reported analyses differ?

The recalculations are simple unadjusted comparisons from the posted group summaries. The registry's reported analyses use the Cochran-Mantel-Haenszel method and express results as percentage treatment differences. In general, the Cochran-Mantel-Haenszel approach combines evidence across strata, whereas a simple unadjusted comparison treats the two groups as aggregate totals. The record does not state which strata were used or provide enough detail to reconstruct the sponsor's analysis. Accordingly, the recalculated estimates are a transparent supplementary analysis, not a replacement for the sponsor's reported analysis.

The reported analysis for two doses versus placebo includes a confidence interval and p-value; the reported one-dose comparison includes a confidence interval but no p-value. The missing p-value for that comparison is not reported in the registry record. A blank reported p-value should not be replaced by the p-value from the unadjusted recalculation, because the methods and potentially the analysis assumptions differ.

Why does the endpoint definition matter?

Statistical results apply to the outcome that was actually defined and recorded. Here, the primary endpoint requires a positive RSV RT-PCR test plus hospitalization for RSV infection or an outpatient visit meeting the specified LRTI criteria. It does not count every RSV-positive test as an event. The precise definition affects which participants qualify, and therefore the resulting percentages and comparisons. The assessment window also matters: the primary outcome covers first study drug administration through Day 150. The results do not directly describe events outside that period.

What does the analysis population tell the reader?

The registry defines the full analysis set as randomized participants who received any study drug, analyzed according to the treatment allocated by the interactive response systems at randomization. This is an as-randomized approach within the stated set. It retains participants in their allocated groups rather than grouping them by treatment actually received. The record does not report how participants with missing endpoint information were handled, whether any participants were excluded after randomization, or the exact analysis denominators for each comparison beyond the arm counts and outcome summaries posted.

These methods explain how to read the estimates; they do not resolve limitations in the record. The original statistical analysis plan, multiplicity procedures, detailed missing-data approach, and the specific stratification used for sponsor analyses are not reported in the registry record.

11. Confidence Intervals and Precision

Precision concerns how tightly the data locate the effect estimate. The recalculated one-dose comparison has a risk difference of -0.003 and a 95% confidence interval from -0.041 to 0.035. The two-dose comparison has a risk difference of 0.011 and a 95% confidence interval from -0.029 to 0.051. Both intervals include zero, the value corresponding to no difference in event proportions. They also span values in both directions, leaving uncertainty about whether the event percentage was lower or higher with suptavumab.

The sponsor's reported confidence intervals likewise include no difference: -4.318 to 3.438 for the one-dose comparison and -2.898 to 5.201 for the two-dose comparison. These are expressed as percentage treatment differences, whereas the recalculated intervals are risk differences on a proportion scale. They should be interpreted within their respective analyses rather than treated as identical estimates.

Confidence intervals provide more information than a threshold-based reading of p-values because they show a range of effect sizes compatible with the data and method. Here, the intervals do not isolate a single direction of effect. The group percentages are also relatively close numerically, but the intervals indicate that a range of differences remains plausible. The registry record does not report a threshold for a clinically important benefit, so statistical precision cannot be translated into a judgment about clinical importance.

Precision is affected by the number of observed events and participants, as well as by the analysis method and outcome variability. General statistical principle: more information often narrows an interval, while sparse outcomes or smaller groups can leave estimates less precise. The primary arm counts are 383, 385, and 381, and the event counts used in the recalculations are 31 and 30 for placebo and one dose, and 31 and 35 for placebo and two doses. These counts help contextualize the estimates, but do not eliminate uncertainty. The intervals describe uncertainty in the estimated group difference, not variation in an individual participant's outcome.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design assumptions. For these binary outcomes, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect. The trial's own original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design that would have an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one. The 90% power column gives the corresponding per-arm planning number for a 90% chance. These are design probabilities under assumptions, not probabilities that the treatment works or that a result from this trial is true. The displayed figures are not observed power.

The rows consider planning for 100%, 75%, and 50% of the observed effect. Smaller effects generally require more participants to distinguish them from no effect with the same nominal power and significance level. That pattern is visible in the very large per-arm illustrations for some comparisons, reflecting the small observed differences in the posted data. The figures are sensitive to the observed effect used as their starting point. A near-zero observed difference can produce especially large planning requirements, so these estimates should not be read as definitive sample-size recommendations.

The planning curve follows the same logic: it depicts how the illustrative participant requirement changes when the assumed effect changes. It is a way to understand the consequences of planning for a smaller or larger effect, not evidence that the original study was designed using these calculations. The registry record does not report the original target number of participants by arm or the assumptions that informed the original design.

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 = 0.081; treatment proportion p₁ = 0.078; average p̄ = 0.079.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3824 = 0.7495.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3824 = 0.3218.
4. n = (0.7495 + 0.3218)² / (-0.0030)² = 126,031.5, rounded up to 126,032 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 <- 0.0809399477806789                          # control proportion
p1 <- 0.0779220779220779                          # 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(2325791)
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 = 126,032 (80% power), 168,720 (90% power)
 75% of observed effect: n per arm = 225,029 (80% power), 301,250 (90% power)
 50% of observed effect: n per arm = 508,501 (80% power), 680,738 (90% power)
power.prop.test: 126031.5 
Simulated power at n = 126,032 per arm: 0.803 (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's sponsor-reported analyses use the Cochran-Mantel-Haenszel method and report percentage treatment differences. For the two-dose comparison with placebo, the reported estimate is 1.15, with a 95% confidence interval from -2.898 to 5.201 and p = 0.577. For the one-dose comparison, the reported estimate is -0.44, with a 95% confidence interval from -4.318 to 3.438; the registry record does not report a p-value for this analysis.

The recalculations use unadjusted risk differences derived from posted group summaries. They are useful for a straightforward comparison of observed proportions, but they are not the same analysis as the sponsor's method. The sponsor's one-dose estimate is negative and its two-dose estimate is positive, matching the broad direction of the unadjusted comparisons, while the numerical estimates and intervals differ. No discrepancy is flagged in the registry record. The sponsor's own analysis therefore remains the principal reported analysis; the recalculations provide a supplementary view, not a correction or substitute.

The registry record does not provide details of any strata or other elements needed to reproduce the Cochran-Mantel-Haenszel results. It also does not report the p-value for the one-dose sponsor analysis. Neither missing detail should be inferred from the unadjusted results.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, treatment comparisons, time points, or analyses are tested. General statistical principle: the more hypotheses examined, the greater the chance that at least one result may appear statistically notable by chance if each is assessed without adjustment. Prespecified testing sequences or multiplicity adjustments can address some of this issue. The registry record lists six outcome measures and four analyses, but does not report a multiplicity adjustment, a testing hierarchy, or the complete set of prespecified analyses. It is therefore not possible to determine from the record whether or how multiplicity was controlled.

The primary endpoint has two suptavumab comparisons against placebo, and the record also includes secondary outcomes. The unadjusted recalculated p-values are descriptive supplementary results; they should not be interpreted as multiplicity-adjusted confirmatory tests. The sponsor reports p = 0.577 for the two-dose comparison and does not report a p-value for the one-dose comparison. The record does not say whether an adjusted p-value or another multiplicity procedure was used for the sponsor analyses.

Missing-data handling is also important for a binary endpoint. The full analysis set includes randomized participants who received any study drug, analyzed according to allocated treatment. However, the registry record does not report how participants with unknown endpoint status, incomplete follow-up, or other missing information were treated. It does not provide a detailed accounting of exclusions from the primary analysis or sensitivity analyses for missing outcomes. The arm counts and posted event summaries do not, by themselves, establish the missing-data assumptions.

The full statistical analysis plan, the original sample-size justification, interim analysis plans, and detailed analysis-population rules are not reported in the registry record. That limits assessment of whether the posted analyses follow a prespecified plan and how robust the findings are to alternative assumptions. These omissions do not change the posted estimates, but they constrain how fully the analysis can be audited or interpreted.

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: respiratory syncytial virus bronchiolitis (3.1%), bronchiolitis (2.4%), respiratory syncytial virus infection (1.2%), bronchitis (1.0%), inguinal hernia (0.9%).

The registry reports serious adverse event counts and numbers at risk separately by study group. In Part A, 0 of 23 participants were reported with a serious adverse event. In Part B, the corresponding figures were 44 of 384 for placebo, 54 of 418 for one-dose suptavumab, and 29 of 348 for two-dose suptavumab. Deaths were reported as 3 in the placebo group, 1 in the one-dose group, and 0 in the two-dose group; no deaths were reported among the 23 Part A participants.

These are descriptive counts, not a comparative safety analysis. The denominators differ across groups, and the registry record does not provide a statistical comparison for these serious adverse event figures. It also does not report the criteria or observation period used for this safety summary in the information. The listed serious adverse event terms include respiratory syncytial virus bronchiolitis, bronchiolitis, respiratory syncytial virus infection, bronchitis, inguinal hernia, and pyrexia, with percentages reported for each term.

The figures should be read as counts recorded in the listed groups, not as proof that one regimen has a higher or lower safety risk. The registry record does not provide enough context to infer causation from these counts.

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

The posted primary results describe the percentage of participants in each Part B group who met a specific medically attended RSV definition through Day 150. The reported percentages were 8.1% with placebo, 7.7% with one dose of suptavumab, and 9.3% with two doses. Both the sponsor-reported and recalculated comparisons have confidence intervals that include no difference. The findings therefore do not establish a clear difference between either suptavumab regimen and placebo on this endpoint.

That interpretation is not equivalent to proving that the regimens are identical or that no difference is possible. The intervals include values in both directions, so uncertainty remains about the magnitude and direction of any difference. Nor does a p-value answer whether an effect is clinically important. The registry record does not report a threshold for clinical importance against which to judge the observed estimates.

The result applies to the trial's stated population, the Part B comparison groups, the endpoint definition, and the follow-up through Day 150. It does not directly answer questions about other age groups, other gestational ages, other RSV seasons, unmeasured outcomes, or follow-up beyond that period. It also does not establish effects on outcomes that were not included in the primary definition, such as every RSV infection or every respiratory illness.

Safety is a separate question from the primary efficacy comparison. The serious adverse event and death counts are descriptive, and the registry record does not provide a formal comparative safety analysis in the information summarized. The primary result should not be used to infer a safety conclusion, just as the safety counts should not be used to determine the primary efficacy effect.

Overall, the registry record supports a cautious description: the observed primary percentages were similar in broad terms, and the available estimates remain uncertain. It does not establish a definitive benefit, harm, or equivalence for either suptavumab regimen on the primary outcome.

18. Why This Trial Matters Statistically

This trial illustrates why an estimated treatment difference should be read alongside its uncertainty. The group percentages alone can make a comparison appear straightforward, but the confidence intervals show that a range of effects remains compatible with the data. A result that does not establish a difference is not the same as evidence of equivalence; equivalence requires a prespecified margin and an analysis designed to assess it, neither of which is reported in the registry record.

The study also highlights the importance of a carefully defined clinical endpoint. The primary outcome required both laboratory confirmation and a specified form of medical attendance, with additional criteria for outpatient LRTI. This definition makes the target question more specific than simply asking whether an infant had RSV, while also making the result dependent on the stated criteria and assessment period.

Comparisons between the sponsor-reported Cochran-Mantel-Haenszel analyses and unadjusted recalculations show why statistical methods and estimands matter. Different approaches can yield somewhat different numerical results even when they use the same posted outcome summaries. The registry record does not include enough detail to reproduce the sponsor analysis fully, so transparent distinctions between the reported analysis and supplementary recalculations are important.

Finally, the planning illustrations demonstrate how small observed effects can translate into large participant requirements when planning to detect still smaller effects. Such illustrations can inform statistical thinking, but they are not evidence of the trial's original design choices or of observed power. The record does not report the original design assumptions, missing-data strategy, or multiplicity procedures, leaving important aspects of the statistical plan unresolved.

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.

Several trial-specific limitations of interpretation follow from what the registry record reports and does not report. The primary comparison is confined to Part B and to the full analysis set of randomized participants who received any study drug. The record does not provide a detailed participant flow, account for missing endpoint status, or describe sensitivity analyses. It is therefore difficult to assess how incomplete follow-up or exclusions may have affected the outcome percentages.

The sponsor's reported primary analyses use the Cochran-Mantel-Haenszel method, but the registry record does not identify the strata or provide enough detail to reproduce the analyses. A p-value is also not reported for the sponsor's one-dose comparison. The original statistical analysis plan, multiplicity handling, interim analyses, and sample-size justification are not reported, limiting a full assessment of prespecification and statistical control.

The primary endpoint is limited to medically attended RSV infection meeting the registry's specified criteria through Day 150. It does not represent every RSV infection or every respiratory event. The record does not report additional adjudication details, nor does it describe how endpoint assessments were handled when required information was unavailable.

Safety counts are presented descriptively, without comparative inference in the record summarized. The listed denominators differ among groups, and the record does not provide a detailed safety analysis plan or enough context to attribute events to study treatment. The findings should therefore not be generalized beyond the outcomes and populations actually reported, and the absence of reported details should not be filled in by assumption.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate the Efficacy and Safety of Suptavumab (REGN2222) for the Prevention of Medically Attended RSV (Respiratory Syncytial Virus) Infection in Preterm Infants — NCT02325791.
• Registry record last updated 2018-11-06; status last verified 2018-10.
• Results first posted 2018-11-06.
• 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

NCT02325791 is a completed Phase 3 randomized, double-blind, placebo-controlled, parallel-group study of suptavumab for prevention of medically attended RSV infection in preterm infants. Overall enrollment was 1177. The primary Part B endpoint was the percentage of participants with a qualifying medically attended RSV infection through Day 150.

The posted primary percentages were 8.1% with placebo, 7.7% with one-dose suptavumab, and 9.3% with two-dose suptavumab. The sponsor-reported and recalculated comparisons both have confidence intervals spanning no difference. The results do not establish a clear difference on the primary endpoint, while leaving uncertainty about the size and direction of any effect.

The registry also reports secondary outcomes and descriptive safety counts. Details of the original sample-size justification, multiplicity procedures, missing-data handling, interim analyses, and the full statistical analysis plan are not reported in the registry record.