Safety of RIV4 Versus IIV4 in Pregnant Women: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety of RIV4 Versus IIV4 in Pregnant Women (NCT03969641), a randomized phase 4 study. The primary outcome is Number of Pregnant Women Vaccinated With RIV4 Versus IIV4 With Adverse Birth Outcomes.

2. Clinical Question

The clinical question concerns the safety comparison of two influenza vaccine formulations during pregnancy. The main endpoint counts participants who experienced at least one qualifying outcome, rather than counting each event separately. That makes the primary result a participant-level comparison of whether any component of the composite occurred.

The registry record describes the trial as randomized, double-masked, and parallel-group. Participants were assigned to RIV4 or IIV4, and vaccines were administered by licensed providers. The study also collected information on local and systemic reactions, antibody titers, and obstetric and neonatal outcomes. Those additional measures provide context for the trial, but the central comparison in this analysis is the composite adverse birth outcome.

The registry record reports 17 participants with the composite outcome among 190 in the RIV4 group and 21 among 192 in the IIV4 group. These counts describe the posted results in the specified analysis population; they do not by themselves establish that the vaccines differ. Interpretation depends on the comparison estimate, its uncertainty, the sponsor’s prespecified analysis, and the details of the endpoint and analysis population.

3. Trial Design

The study is recorded as a completed Phase 4, prospective, randomized clinical trial sponsored by Duke University. It used a parallel-group design with double masking. The registry record lists enrollment of 384. Randomization was described in the study summary as 1:1 allocation to quadrivalent recombinant influenza vaccine (RIV4) or quadrivalent inactivated influenza vaccine (IIV4), administered by licensed providers.

The study population for the primary outcome is described as the mITT population: participants who were enrolled, randomized, and received study vaccine. The posted primary endpoint counts participants experiencing at least one of the defined adverse birth outcomes. Its timeframe is stated as outcomes monitored within postnatal day 28. The endpoint description defines preterm birth as live birth before 37 weeks and 0 days of gestation, spontaneous abortion as pregnancy loss before 20 weeks and 0 days, fetal death as intrauterine death at or after 20 weeks and 0 days, and neonatal death as infant death within the first 28 days of life.

Study procedures described in the registry include assessment of injection-site and systemic reactions on vaccination day and during the 8 days following vaccination, using web-based or paper diaries. Maternal serum was to be collected before vaccination and approximately 29 days after vaccination for influenza antibody titers. When feasible, maternal blood at delivery and cord blood serum were also to be analyzed. The summary states that participants were followed through delivery and that obstetric and neonatal outcomes were obtained from medical record review for 90 days of life.

The listed study dates are 2019-09-05 for study start and 2021-09-29 for primary completion; the status is completed. The registry record does not report the trial’s original sample-size assumptions or a complete account of its statistical analysis plan.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: mITT Population- any participant that was enrolled, randomized into the study, and received study vaccine

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: Participants who received study product.

6. Primary Endpoint

The registry lists the primary outcome as Number of Pregnant Women Vaccinated With RIV4 Versus IIV4 With Adverse Birth Outcomes, measured over Birth outcomes were monitored within postnatal day 28..

The primary endpoint is the number of pregnant participants with at least one adverse birth outcome in a composite of preterm birth, spontaneous abortion, fetal death, or neonatal death. The registry defines these outcomes by gestational age or timing after birth. Because the measure is a count of participants with an event, a participant with more than one component still contributes to the composite as a participant experiencing an outcome; the endpoint is not a count of all component events.

A composite endpoint can summarize several clinically important outcomes in a single comparison. It may also increase the number of participants who meet the endpoint compared with considering a less frequent component alone. However, the components may differ in nature and frequency, so a composite estimate does not tell whether each component has the same pattern. Component-specific results are useful context, but they should not be treated as interchangeable with the primary composite.

The registry specifies the primary population as participants who were enrolled, randomized, and received study vaccine. The primary timeframe is stated as monitoring birth outcomes within postnatal day 28. These definitions matter because a participant’s eligibility for the analysis and the period over which outcomes are counted determine what the event rate represents. The primary counts are 17 of 190 for RIV4 and 21 of 192 for IIV4. The counts alone do not quantify the precision of the comparison; that requires an effect estimate and its confidence interval.

7. Results Posted in the Registry

• IIV4: 10.9% (21/192) versus 8.9% (17/190) on control; risk difference 2.0 percentage points (95% CI -4.0 to 8.0), risk ratio 1.22 (0.67–2.24); unadjusted two-proportion z-test p = 0.516.

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 Pregnant Women With Preterm Birth After RIV4 Versus IIV4 Vaccination

• 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:
  • IIV4: 9.9% (19/192) versus 7.4% (14/190) on control; risk difference 2.5 percentage points (95% CI -3.1 to 8.2), risk ratio 1.34 (0.69–2.60); unadjusted two-proportion z-test p = 0.379.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between IIV4 and the control. The interval gives the range of effects that remain compatible with the data.

Number of Pregnant Women With Fetal or Neonatal Death After RIV4 Versus IIV4 Vaccination

• 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:
  • IIV4: 0.0% (0/192) versus 1.1% (2/190) on control; risk difference -1.1 percentage points (95% CI -2.5 to 0.4); unadjusted two-proportion z-test p = 0.154.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between IIV4 and the control. The interval gives the range of effects that remain compatible with the data.

Number of Pregnant Women With Spontaneous Abortion After RIV4 Versus IIV4 Vaccination

• 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:
  • IIV4: 2.8% (2/72) versus 1.6% (1/62) on control; risk difference 1.2 percentage points (95% CI -3.8 to 6.1), risk ratio 1.72 (0.16–18.54); unadjusted two-proportion z-test p = 0.649.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between IIV4 and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes address specific birth outcomes and solicited reactions rather than the primary composite alone. Their overall pattern is not a uniform finding of a clear group difference: the posted comparisons are imprecise, and the event counts for some outcomes are sparse. These component outcomes help describe the range of events captured by the study, but they should be read as supporting context rather than as independent confirmation of the primary result.

Secondary outcomes are related to the primary endpoint because preterm birth, spontaneous abortion, and fetal or neonatal death overlap with components of the composite. However, a component-specific analysis uses a narrower outcome and can involve a different eligible population or timeframe. For example, the spontaneous-abortion analysis uses the participants listed for that endpoint, rather than the primary analysis population. Component results therefore cannot simply be substituted for the composite result or interpreted as if all analyses had identical denominators and follow-up.

The registry posts 17 analyses and four secondary outcomes. Multiple outcomes and analyses create opportunities for apparently notable results to arise by chance, particularly when many comparisons are considered. The registry record does not report a multiplicity adjustment for the secondary outcomes. Their p-values should consequently be treated as unadjusted evidence and interpreted cautiously, not as definitive tests standing alone. The posted secondary analyses can identify patterns that merit attention, but they do not resolve the uncertainty around the primary comparison.

There is also no basis for treating the secondary outcomes as a single combined test: the outcomes differ in definition, timeframe, and event frequency. The overall reading is that these analyses add descriptive detail, while limited events and multiplicity reduce the weight that should be attached to any isolated comparison. The primary endpoint and the sponsor’s stated analysis remain central to the trial’s main inferential claim.

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

• Number of Pregnant Women With Preterm Birth After RIV4 Versus IIV4 Vaccination
• Number of Pregnant Women With Fetal or Neonatal Death After RIV4 Versus IIV4 Vaccination
• Number of Pregnant Women With Spontaneous Abortion After RIV4 Versus IIV4 Vaccination
• Number of Pregnant Women With Moderate/Severe Solicited Reactogenicity Events (Local and Systemic) Within 8 Days After Vaccination With RIV4 Versus IIV4

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary endpoint, each participant is classified as having or not having the event. The primary endpoint is a participant count for a composite adverse birth outcome, so the basic descriptive information is the event count and the number of participants in each group. The posted counts are 17 of 190 for RIV4 and 21 of 192 for IIV4. The comparison is not a comparison of average event severity or of time until an event.

What does a risk difference describe?

A risk difference subtracts the event proportion in one group from the event proportion in the other. Its units are an absolute difference in proportions. The recalculated primary contrast is expressed as IIV4 minus RIV4 and is 0.020. A positive value in that ordering means the posted event proportion is higher in IIV4; a negative value would mean it is higher in RIV4. The estimate is a summary of the observed groups, not a guarantee that the same difference would occur in another study.

The posted recalculation is unadjusted: it uses the group summary counts without a reported adjustment for other variables. The registry’s sponsor-reported primary analysis instead names the Cochran-Mantel-Haenszel method. This is a stratified method for comparing groups while accounting for strata, when such strata are part of the analysis. The registry record does not state the stratification variables or provide enough details to reconstruct the sponsor’s calculation. The sponsor-reported difference is RIV4 minus IIV4, whereas the simple recalculation uses IIV4 minus RIV4, and the estimates do not otherwise match. The sponsor’s own analysis takes precedence when describing the trial’s reported inferential result.

How should a confidence interval be read?

A confidence interval describes the range of estimates compatible with the data and the specified statistical method, under that method’s assumptions. It communicates precision as well as direction. A narrow interval indicates greater precision than a wide interval on the same scale. For the unadjusted primary risk difference, the 95% interval is -0.040 to 0.080. Because it spans zero, the data are compatible with no absolute difference as well as with differences in either direction. The interval is not a probability statement that the true value has a specified chance of lying inside these particular bounds.

A p-value measures how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the model used. The recalculated primary p-value is 0.516. It does not measure the probability that the null hypothesis is true, and it does not establish equivalence. The sponsor’s analysis reports a non-inferiority test with p < 0.001, but interpretation of non-inferiority depends on the margin and the analysis definition. The margin is not reported in the registry record.

Why are the methods not interchangeable?

A direct recalculation from posted counts may not reproduce an analysis that uses stratification, a different contrast orientation, or other analysis choices. In this trial, the registry identifies the sponsor’s primary method as Cochran-Mantel-Haenszel, while the recalculation is an unadjusted risk-difference comparison. The registry record does not report sufficient detail to determine which analytic features account for the discrepancy. The estimates should therefore be labelled according to their source, rather than combined or selectively treated as if they were the same analysis.

The endpoint is a composite, and its components are binary outcomes recorded over defined periods. Combining them provides a single primary comparison, but a composite can conceal differences in component patterns. The posted secondary outcomes separate some components, including preterm birth, fetal or neonatal death, and spontaneous abortion. They are useful for understanding what contributes to the broad endpoint, but they do not have the same status as the primary analysis.

Why can over-dispersion matter?

Over-dispersion is a general concern in some count models when the observed variability is greater than the model assumes. In a simple binary participant-level comparison, the central issue is the event proportion and its uncertainty; the primary endpoint is not reported as a recurrent-event count. There is no dispersion estimate reported for this endpoint, and the registry does not describe a model that addresses over-dispersion. It would not be appropriate to infer that such a model was used.

The reported methods are therefore best read as two distinct products: the sponsor’s stated stratified non-inferiority analysis, and an unadjusted recalculation from posted summary counts. The former is the trial’s reported analysis; the latter offers a transparent check based on the displayed counts. Neither should be expanded into claims about unreported adjustments, covariates, or prespecified decisions.

11. Confidence Intervals and Precision

The unadjusted primary risk-difference estimate is 0.020, with a 95% confidence interval from -0.040 to 0.080. The interval crosses zero and spans values favoring either group. Its breadth indicates that the posted summary counts do not pin down the absolute difference very precisely. The point estimate is only one value within a wider range of estimates compatible with the data and the calculation method.

The interval should be interpreted on the risk-difference scale, not as a relative effect. It expresses an absolute contrast between the event proportions in the groups. The lower and upper limits are not predictions for individual participants, and the interval does not establish that all values within it are equally plausible. It also does not assign a probability to the true effect after observing these data.

The sponsor’s primary analysis reports a 97.5% confidence interval with upper bound 0.041; its lower bound is not reported in the registry record. That reported analysis is labelled non-inferiority. Without the lower bound and the non-inferiority margin, the full criterion cannot be assessed from the registry entry. Its result should be kept distinct from the unadjusted 95% interval, which is based on a different calculation and direction of contrast.

Precision is limited by how much information the data contain about the outcome. The primary endpoint counts are modest, and the confidence interval reflects uncertainty around the difference. A point estimate near zero together with a broad interval should not be described as proof of no difference. Similarly, an interval that permits effects in either direction does not by itself show that either effect is likely. These intervals describe statistical uncertainty under their respective methods, not the clinical importance of every value they contain.

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 planning illustrations translate an assumed effect into the number of participants per arm that a hypothetical study would require under the stated assumptions. For this primary binary outcome, the figures are participants per arm, not total events. The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The registry record does not report the assumptions used for the trial’s original design.

The 80% power column describes the planned chance of detecting the specified effect under the assumptions if that effect were the true effect. The 90% power column uses a higher target chance of detection, which generally requires a larger planned sample. For the primary endpoint, the planning values are 3,548 participants per arm for 80% power and 4,749 for 90% power when planning for 100% of the observed effect. Planning for 75% of the observed effect gives 6,168 and 8,256 participants per arm; planning for 50% gives 13,559 and 18,151.

Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm as the assumed effect becomes smaller. These calculations are planning illustrations based on the observed effect, not observed power. They do not describe the probability that the completed trial’s result is correct, and they should not be used as a substitute for the trial’s original design rationale, which is not reported in the registry record.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.089; treatment proportion p₁ = 0.109; average p̄ = 0.099.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4232 = 0.8294.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4229 = 0.3560.
4. n = (0.8294 + 0.3560)² / (0.0199)² = 3,547.7, rounded up to 3,548 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 <- 0.0894736842105263                          # control proportion
p1 <- 0.109375                          # 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(3969641)
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 = 3,548 (80% power), 4,749 (90% power)
 75% of observed effect: n per arm = 6,168 (80% power), 8,256 (90% power)
 50% of observed effect: n per arm = 13,559 (80% power), 18,151 (90% power)
power.prop.test: 3547.7 
Simulated power at n = 3,548 per arm: 0.801 (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 primary analysis is sponsor-reported as a Cochran-Mantel-Haenszel non-inferiority analysis. It gives a RIV4-minus-IIV4 difference in proportions of -0.021, an upper 97.5% confidence limit of 0.041, and p < 0.001. The lower confidence limit and the non-inferiority margin are not reported in the registry record, limiting independent assessment of the stated non-inferiority result.

The unadjusted recalculation from the posted counts instead gives an IIV4-minus-RIV4 risk difference of 0.020, a 95% confidence interval from -0.040 to 0.080, and p = 0.516. The contrast is written in the opposite direction, and its estimate and uncertainty are not the same as the sponsor’s. The recalculation uses the posted group counts without the sponsor’s named stratified method, and the registry record does not explain the discrepancy.

These results should not be blended into a single estimate or used selectively. The sponsor’s own analysis takes precedence as the trial’s reported inferential analysis. The recalculation is a simple, unadjusted check of the summary counts and highlights that analytic choices matter. It cannot establish why the two analyses differ or supply missing information about the sponsor’s method, strata, or non-inferiority margin.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes and analyses. When many hypotheses are examined, the chance of obtaining at least one apparently unusual result by chance can increase. Statistical methods can address this multiplicity by adjusting significance thresholds, controlling error rates, or defining a hierarchy of tests. Whether such an approach was used for the secondary analyses is not reported in the registry record. The posted secondary p-values should therefore be regarded as unadjusted unless the registry explicitly identifies otherwise.

The registry does identify the primary analysis as non-inferiority and names a Cochran-Mantel-Haenszel method. It does not report the non-inferiority margin, the full lower confidence limit, or sufficient detail about stratification to reconstruct the analysis. The original sample-size justification, any interim analyses, and the complete statistical plan are also not reported in the registry record. Those omissions limit independent assessment of the confirmatory framework and of how each analysis was selected or interpreted.

The primary population is described as mITT: enrolled participants randomized and receiving study vaccine. The registry record does not fully describe missing outcome data, exclusions from each analysis, or the handling of participants whose outcomes could not be determined. It also does not report whether the primary analysis used additional populations as sensitivity analyses. Missingness can affect a binary endpoint if outcome status is not equally observed or if analytic handling is related to group or outcome risk, but the available record does not establish whether that occurred.

These are reporting limitations, not proof that the trial’s analysis was inappropriate. A complete evaluation would require the prespecified analysis details, definitions for analysis populations, missing-data procedures, multiplicity approach, and non-inferiority margin. Without those details, the safest interpretation is to distinguish the reported sponsor analysis from the unadjusted recalculation and to avoid treating exploratory or unadjusted secondary findings as definitive.

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: preeclampsia (2.6%), intrauterine fetal demise (1.1%), spontaneous abortion (1.0%), ventricular septal defect (1.0%), opioid dependence relapse (0.5%).

The registry’s serious adverse event summary lists 14 affected participants among 190 at risk in the RIV4 group and 12 among 192 at risk in the IIV4 group. The other adverse-event summary lists 22 affected participants in each group, with 190 and 192 at risk, respectively. The registry also records 2 deaths for RIV4 and 0 for IIV4. These are descriptive counts; the registry entry does not establish that an event was caused by vaccination.

The listed serious terms include Preeclampsia at 2.6%, Intrauterine Fetal Demise at 1.1%, Spontaneous Abortion at 1.0%, ventricular septal defect at 1.0%, Opioid Dependence Relapse at 0.5%, and Vomiting at 0.5%. These are the registry’s reported percentages for terms, not a basis for inferring comparative risk or causation. The entry does not provide a detailed account of event adjudication or a causal assessment for each term.

Safety counts require attention to the event definition, the time period, the population at risk, and whether the figures refer to participants or events. The displayed summary is not a substitute for the primary adverse birth outcome analysis, and the adverse-event counts should not be interpreted as proof that either vaccine is safer. Differences in counts can reflect chance as well as underlying differences; the registry summary alone does not resolve those possibilities.

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

The registry’s posted primary counts describe how many participants in each randomized group experienced at least one component of the adverse birth outcome composite. The unadjusted recalculation yields a risk difference of 0.020 for IIV4 minus RIV4, with a 95% confidence interval from -0.040 to 0.080. This estimate is uncertain and compatible with differences in either direction. It does not establish equivalence, and the recalculated p-value of 0.516 is not evidence that the true difference is exactly zero.

The sponsor’s reported primary analysis is labelled non-inferiority and reports p < 0.001. Because the non-inferiority margin and lower confidence bound are not reported in the registry record, the criterion cannot be fully checked from the posted information. In addition, the sponsor estimate differs from the unadjusted recalculation. The sponsor’s own analysis takes precedence as the trial’s reported inferential result, but the missing details and discrepancy should remain part of the interpretation.

The endpoint is a composite, so it does not show whether each component has the same pattern. The secondary outcomes add information about individual components and other safety measures, but they are not a replacement for the primary endpoint. Multiple secondary analyses without a reported multiplicity adjustment are less conclusive, and sparse counts can yield wide uncertainty.

These data describe outcomes in this completed trial and its specified population and follow-up. They do not establish a general treatment effect across other populations, vaccine products, or clinical settings. They also do not show that an individual outcome was caused by vaccination. The findings should be understood as an estimate with statistical uncertainty and reporting limitations, not as medical advice or a definitive judgment about the safety of either vaccine.

18. Why This Trial Matters Statistically

This trial illustrates why a result should be read through both its clinical definition and its statistical analysis. The primary outcome is not a single event but a composite of preterm birth, spontaneous abortion, fetal death, and neonatal death. That construction provides a broad participant-level safety measure, while also making it important to inspect component outcomes and avoid assuming that one component represents the whole endpoint.

It also illustrates the difference between a sponsor-reported inferential analysis and a transparent recalculation from summary counts. The registry labels the sponsor’s analysis as non-inferiority and names a Cochran-Mantel-Haenszel method. The simple recalculation uses an unadjusted risk difference and yields a different estimate and p-value. Keeping the analysis source, contrast direction, and method explicit prevents one result from being mistaken for another. The discrepancy is meaningful for interpretation even though the registry does not explain its cause.

Confidence intervals are particularly important in a safety comparison. A point estimate alone can suggest a direction, but uncertainty determines how much precision the data provide. The unadjusted interval includes zero and a range of effects in either direction; it should not be turned into a claim of equivalence. For a non-inferiority claim, the margin is essential to interpretation, yet it is not reported in the registry record.

Finally, secondary outcomes and safety summaries can add context without becoming definitive evidence for each separate comparison. Outcome multiplicity, differing timeframes, and sparse event counts all affect how much weight to place on those results. The trial is statistically informative because it demonstrates these interpretive issues in a randomized maternal-safety study, while the available registry information also shows why complete reporting of analysis choices is necessary for independent evaluation.

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 are specific to the information reported for this trial. The sponsor’s primary non-inferiority analysis includes an upper 97.5% confidence bound, but its lower bound is not reported in the registry record. The non-inferiority margin is also not reported. Without these details, the central non-inferiority criterion cannot be independently evaluated from the registry entry.

The unadjusted recalculation from the posted counts differs from the sponsor’s estimate and inference. The reported sponsor method is Cochran-Mantel-Haenszel, while the recalculation is based on the summary counts without adjustment. The registry record does not explain the discrepancy or state the relevant stratification details, so its source cannot be determined. The recalculated analysis is therefore best treated as a check of the posted counts, not as a substitute for the sponsor’s analysis.

The outcome is a composite, and the registry’s secondary component analyses involve different event definitions and in some cases different analysis populations or timeframes. The number of events for some outcomes is limited, which constrains precision. The registry record does not report a multiplicity adjustment for the secondary analyses, so isolated secondary p-values warrant caution.

Further details on missing outcome data, exclusions, outcome ascertainment completeness, and sensitivity analyses are not reported in the registry record. Nor are the trial’s original sample-size justification, interim analyses, and full statistical plan reported. These gaps limit assessment of how well the posted analyses reflect the prespecified design. They do not establish that the data are biased, but they restrict independent verification and narrow the conclusions that can be drawn from the registry results alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety of RIV4 Versus IIV4 in Pregnant Women — NCT03969641.
• Registry record last updated 2023-01-11; status last verified 2023-01.
• Results first posted 2022-12-27.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed, randomized, double-masked, parallel-group Phase 4 trial sponsored by Duke University. It compared RIV4 with IIV4 in pregnant women and lists enrollment of 384. The study began on 2019-09-05 and reached primary completion on 2021-09-29.

The primary endpoint counted participants with at least one adverse birth outcome in a composite of preterm birth, spontaneous abortion, fetal death, or neonatal death. Posted counts were 17 of 190 for RIV4 and 21 of 192 for IIV4. The sponsor reported a Cochran-Mantel-Haenszel non-inferiority analysis; an unadjusted recalculation from the counts differs, and the registry record does not report the margin needed to evaluate the non-inferiority criterion fully.

The record also includes secondary birth outcomes and adverse-event summaries. Interpretation is limited by missing analysis details, including the non-inferiority margin, the full sponsor confidence interval, and the handling of missing data and multiplicity.