Echocardiography Sub-Study of the Umbilical Cord Milking in Non-Vigorous Infants Trial (MINVI): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Echocardiography Sub-Study of the Umbilical Cord Milking in Non-Vigorous Infants Trial (MINVI) (NCT03798093), a randomized na study. The primary outcome is Left Ventricular Output.

2. Clinical Question

3. Trial Design

This completed echocardiography sub-study is titled the Echocardiography Sub-Study of the Umbilical Cord Milking in Non-Vigorous Infants Trial (MINVI). Its official title is Hemodynamic Changes With Umbilical Cord Milking in Nonvigorous Newborns. Sharp HealthCare is listed as the sponsor. The registry classifies the study as randomized, single masked, and crossover, with phase listed as not applicable.

The record gives an enrollment of 227. It describes non-vigorous infants enrolled in MINVI being approached for consent for ongoing data collection, with an optional echocardiogram if a parent consented. The reported primary endpoint is left ventricular output, and four secondary measures are listed: right ventricular output, superior vena cava flow, peak systolic strain, and peak systolic velocity. The posted endpoint results give group counts of 106 for umbilical cord milking and 121 for early cord clamping. These endpoint counts should not be taken as a description of all participants enrolled or of the consent process.

The registry classifies the model as crossover, but the sequence, periods, and handling of any within-participant measurements are not reported in the registry record. The record also does not explain how single masking was implemented or identify who was masked. The listed dates are a study start of 2019-01-07, primary completion of 2021-06-01, and completed status. The protocol, eligibility criteria beyond the description of non-vigorous infants, and the original design assumptions are not reported in the registry record. These omissions limit what can be inferred about allocation procedures, participant flow, and the intended analysis.

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: The two hospitals who participated in the echocardiography sub-study and were both randomized to implement umbilical cord milking in the initial period (Period 1) and randomized to implement early cord clamping in the cross over period (Period 2).

Initial Randomized Intervention

Crossover Randomized Intervention

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 Left Ventricular Output, measured over 12 ± 6 hours of life.

Left ventricular output is the amount of blood pumped by the left ventricle, expressed in the registry as mL/kg/min. The listed measurement was obtained by cardiac ultrasound at 12 ± 6 hours of life. The registry reports a mean and standard deviation for each group. A mean describes the group’s average measurement, while the standard deviation describes how spread out individual measurements are around that average.

This endpoint is one way to quantify cardiac blood flow during the stated measurement window. It is used in this sub-study to compare hemodynamic measurements between the two assigned cord-management groups. The endpoint alone does not establish why any group difference occurred, whether a difference is clinically important, or whether it predicts later outcomes. Those interpretations would require context and information beyond the registry result, including how the measurements were obtained, the analysis population, and any relationship to outcomes that matter to families and clinicians.

The primary result is a comparison of group averages, not a result for every newborn. The registry does not report a threshold for a meaningful difference, the distribution of individual measurements beyond the standard deviations, or a clinically meaningful interpretation of the endpoint. The stated measurement window also allows variation in the timing of echocardiography. How that timing was incorporated into the analysis is not reported in the registry record.

7. Results Posted in the Registry

• Early Cord Clamping - Neonate: mean 187.00 versus 225.00 on control; difference -38.00 (95% CI -53.31 to -22.69), standardized effect d = -0.66; 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.

Neonatal Right Ventricular Output

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Early Cord Clamping - Neonate: mean 222.00 versus 284.00 on control; difference -62.00 (95% CI -85.82 to -38.18), standardized effect d = -0.68; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Early Cord Clamping - Neonate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Neonatal Superior Vena Cava Flow

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Early Cord Clamping - Neonate: mean 86.00 versus 100.00 on control; difference -14.00 (95% CI -23.89 to -4.11), standardized effect d = -0.37; z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Early Cord Clamping - Neonate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Neonatal Peak Systolic Strain

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Early Cord Clamping - Neonate: mean -22.00 versus -17.00 on control; difference -5.00 (95% CI -5.78 to -4.22), standardized effect d = -1.67; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Early Cord Clamping - Neonate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary endpoint means follow a broadly consistent directional pattern: the early cord clamping group has lower posted means for right ventricular output and superior vena cava flow, and a more negative mean for peak systolic strain. The unadjusted recalculations also yield intervals that exclude zero for these three measures. This general pattern is compatible with the direction of the primary group-mean comparison, but it does not resolve the discrepancy between the primary recalculation and the sponsor’s reported analysis.

The registry lists four secondary outcomes, including peak systolic velocity, but only three have posted results in the secondary endpoint data. Results for peak systolic velocity are not reported in the registry record. No sponsor-reported analyses are listed for the posted secondary measures. The available secondary comparisons are therefore recalculations from summary statistics, rather than reported sponsor-model estimates.

Secondary findings generally carry less weight than a prespecified primary analysis, particularly when several outcomes are examined. In general, testing multiple endpoints increases the chance that some results will appear statistically notable by chance. The registry does not report whether the secondary analyses were prespecified in detail, whether multiplicity was addressed, or how missing endpoint results were handled. Their unadjusted p-values should consequently be read as exploratory evidence rather than as confirmatory tests.

These endpoints are related measures of cardiovascular function, but the record does not describe a composite outcome, a hierarchy among secondary outcomes, or a method for combining them. Their pattern can provide context for the primary endpoint, but it cannot establish a broader clinical effect or make the primary discrepancy disappear. Interpretation also depends on measurement quality, timing, and analysis-population details that are not reported in the registry record.

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

• Neonatal Right Ventricular Output
• Neonatal Superior Vena Cava Flow
• Neonatal Peak Systolic Strain
• Neonatal Peak Systolic Velocity

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a measured quantity that can take a range of values rather than a set of categories. The registry reports the mean and standard deviation for each group. The mean is a measure of the group’s center. The standard deviation describes variation among measurements within that group; it is not the uncertainty in the estimated mean difference. A standard error is used to describe uncertainty in an estimate, while a confidence interval presents a range of values compatible with the data and the analysis assumptions.

What does the recalculated mean difference represent?

The posted comparison is expressed as early cord clamping minus umbilical cord milking. On that scale, a negative value means the posted mean is lower in the early-clamping group. The unadjusted recalculation uses the group means and their reported variability to estimate a difference and its uncertainty. It does not incorporate covariates, account for a crossover structure, or reproduce an unreported regression model. It is consequently a simple comparison of the posted summaries, not a substitute for the sponsor’s analysis.

For the primary measure, the unadjusted recalculation gives a mean difference of -38.0 mL/kg/min and a 95% confidence interval from -53.31 to -22.69. The interval excludes zero, and the reported unadjusted p-value is < 0.001. These statistics describe the recalculation, not the sponsor’s reported model. The sponsor’s linear regression result is -0.112 with a 95% confidence interval from -29.3 to 1.7 and p = 0.08. The mismatch is substantial enough that the sponsor’s result takes precedence. The registry does not supply the model details needed to determine whether differences in adjustment, coding, analytic population, or another feature explain it.

How should a confidence interval be read?

A confidence interval expresses uncertainty around an estimated effect under the assumptions of the method used. A narrower interval indicates greater precision than a wider interval, all else equal. If an interval includes zero for a mean difference, the data and method do not rule out no difference at the corresponding confidence level. An interval that excludes zero is evidence against a zero difference under that calculation, but it does not by itself establish clinical importance or remove bias and design concerns.

The p-value measures how unusual the data, or more extreme data, would be under a specified null hypothesis and the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. Because the primary recalculation and sponsor model yield different results, their p-values answer questions under different calculations and should not be blended into a single conclusion.

Why might analysis structure matter?

The registry calls the study model crossover. In general, a crossover design can involve measurements under more than one condition, making the relationship between observations from the same participant important. Appropriate analysis may need to reflect within-participant dependence and the sequence or period of measurements. The record does not report the crossover sequence, whether participants contributed measurements under both conditions, or how any dependence was handled. Thus the model label alone is insufficient to assess whether the posted regression accounts for the study structure.

Optional echocardiography and parental consent also matter for interpretation. In general, if having a measurement is related to participant characteristics or clinical circumstances, the analyzed group may differ from all enrolled participants. The registry does not report how many were approached, consented, had usable echocardiograms, or were included in each analysis, and it does not describe missing-data methods. It is therefore not possible to assess selection or missing-measurement effects from the record.

What do the planning calculations mean?

The sample-size illustrations use the observed effect as a starting point and consider fractions of that effect. Their stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. These calculations are planning illustrations, not the original trial design. The original design assumptions and sample-size justification are not reported in the registry record. The figures describe participants per arm for continuous outcomes; the general convention for time-to-event outcomes would instead be total events, but the outcomes are continuous.

Over-dispersion is a general concern when observed variability exceeds what a model assumes. In that situation, uncertainty can be understated if the analysis does not accommodate the extra variability. The record reports standard deviations for the group summaries but does not give enough model detail to assess how variability, dependence, or any departures from assumptions were handled in the sponsor analysis. The recalculations also depend on assumptions about the summary statistics and do not resolve those uncertainties.

11. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is determined by the data and analysis. For the primary endpoint, the unadjusted recalculation gives a 95% confidence interval from -53.31 to -22.69 mL/kg/min around the mean difference of -38.0 mL/kg/min. That interval excludes zero. It describes uncertainty under the simple recalculation, not the sponsor’s regression analysis.

The sponsor-reported 95% confidence interval runs from -29.3 to 1.7, with a reported value of -0.112. It spans zero, so the analysis is compatible with no difference as well as values on either side of zero under its model. The discrepancy between this interval and the recalculated interval cannot be resolved using the registry record; the sponsor’s own analysis takes precedence. The point estimate and interval should be reported together, rather than relying on the p-value alone.

For continuous outcomes, confidence intervals are expressed in the units of the endpoint and give a range for the mean difference. Their width depends on the amount of variation, the information available, and the analysis method. A confidence interval is not a range expected to contain most individual newborns’ measurements. The standard deviations describe within-group spread, while the intervals describe uncertainty in a group comparison.

Even a relatively precise estimate would not by itself show that a difference matters clinically. The registry does not specify a threshold for clinical importance, and it does not provide enough information to evaluate the precision of the sponsor model beyond its reported interval. Consent for optional echocardiography, unavailable analysis-population details, and the unexplained crossover classification also limit confidence in interpreting precision as applying to all enrolled newborns.

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 are expressed as participants per arm for these continuous outcomes, not as total events. They use the observed effect as a reference and show planning for 100%, 75%, and 50% of that effect. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The original trial design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions are correct. The 90% power column gives the corresponding planning target for a 90% chance. These are prospective planning quantities: they are not the probability that the observed result is correct or that the study has found a real effect. They are not observed power.

The illustrations show that smaller target effects require more participants per arm, because a smaller difference is harder to distinguish from random variation. For example, the planning targets for 50% of the observed primary effect are larger than those for 100% of the observed effect. This does not mean that the trial was designed around any of those effects. Nor does it establish that the observed effect is likely to recur in another study. The calculations are illustrations based on the observed result, and the primary result itself has a discrepancy between the sponsor’s analysis and the unadjusted recalculation.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -38.000; pooled standard deviation σ = 57.910.
2. n = 2 × (1.96 + 0.842)² × 57.910² / -38.000² = 36.5, rounded up to 37 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
delta <- -38                      # observed difference in means
sigma <- 57.9102754267323                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3798093)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 37 (80% power), 49 (90% power)
 75% of observed effect: n per arm = 65 (80% power), 87 (90% power)
 50% of observed effect: n per arm = 146 (80% power), 196 (90% power)
power.t.test: 37.4 
Simulated power at n = 37 per arm: 0.794 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor reports a linear regression analysis using least squares for the primary comparison. Its reported value is -0.112, with a 95% confidence interval from -29.3 to 1.7 and p = 0.08. The unadjusted recalculation from the posted group means and standard deviations instead gives a mean difference of -38.0 mL/kg/min, a 95% confidence interval from -53.31 to -22.69, and p < 0.001. The registry flags a discrepancy between the analyses.

The recalculation is a simple, unadjusted comparison of group summaries. It does not reproduce the sponsor’s regression model or account for model details not reported in the registry. The sponsor’s result therefore takes precedence over the recalculated result. The reported confidence interval includes zero, whereas the recalculated interval does not. This difference changes the statistical reading, not just the apparent precision.

The record does not explain the estimate’s scale, model specification, covariate adjustment, analysis population, or how the crossover classification was handled. Without those details, it is not possible to reconcile the sponsor’s reported value with the group-summary comparison. The sound reading is to present the sponsor’s analysis as the registry-reported analysis and identify the recalculation as an unadjusted check, without treating the latter as a replacement.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and multiple secondary outcomes, but it does not report a multiplicity strategy. When several outcomes are tested, the chance of at least one apparently unusual result can increase. General approaches include adjusting the testing threshold or specifying a testing hierarchy in advance. Neither approach is described in the registry record, so the posted unadjusted secondary p-values should not be treated as if they were protected against multiple comparisons.

The record also does not report the analysis population in enough detail to determine who contributed to each endpoint. Although endpoint summaries list group counts, the record does not explain how those counts relate to enrollment, consent for optional echocardiography, successful measurement, or inclusion in the sponsor’s regression. It does not report participant flow from approach to analysis or reasons measurements may have been unavailable.

Missing-data methods are not reported in the registry record. In general, missing measurements can affect a comparison if missingness is related to group assignment, clinical condition, or the measurement itself. Without the extent and pattern of missingness or the methods used to address it, the impact cannot be assessed. The record also does not state whether the reported analysis followed an intention-to-treat approach or another analysis-population definition.

The crossover classification raises additional questions about the unit and structure of analysis. Sequence, period, within-participant measurements, and any carryover considerations are not reported. The record does not specify whether the regression included terms for these features. These gaps do not establish that the analysis was inappropriate; they mean its suitability cannot be evaluated fully from the registry information. The discrepancy between the sponsor result and the unadjusted recalculation further emphasizes the importance of a complete analysis description.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry reports zero serious adverse events in the umbilical cord milking group and zero in the early cord clamping group. It also reports zero other adverse events in both groups and zero deaths in both groups. The listed groups at risk are 106 for umbilical cord milking and 121 for early cord clamping. No serious adverse event terms are listed.

These figures describe the adverse-event fields posted in the registry record. They do not establish that no adverse events of any kind occurred, that all participants were observed for the same duration, or that the groups have identical safety profiles. The record does not report the event definitions, ascertainment period, completeness of reporting, or detailed methods for collecting adverse events. The zero counts should therefore be read as the registry’s reported counts, not as proof of absence of risk.

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

The posted group summaries show different average echocardiographic measurements between the cord-management groups at the stated measurement window. For the primary outcome, the mean is higher in the umbilical cord milking group than in the early cord clamping group. A direct unadjusted recalculation yields an interval excluding zero, while the sponsor’s reported regression yields an interval that includes zero. Because these analyses disagree, the sponsor’s own analysis takes precedence, and the discrepancy remains unresolved by the registry record.

The findings concern measurements at 12 ± 6 hours of life. They do not, on their own, show what caused the group differences, whether any difference is clinically important, or whether it predicts later health outcomes. The registry does not provide a threshold for meaningful change or report longer-term outcomes in the material described. A group average also does not describe every individual newborn.

These results should not be interpreted as advice about cord management or as evidence that one approach does or does not work. The sub-study involved an optional echocardiogram requiring parental consent, and the record does not provide sufficient information about who had measurements available or how missing data were handled. The crossover model label is not accompanied by details about sequence or analysis. Those gaps, as well as the unexplained difference between the sponsor analysis and recalculation, limit the conclusions that can be drawn from the posted statistics.

The secondary endpoint pattern offers additional descriptive context, but the secondary analyses are unadjusted and no sponsor-reported analyses are listed for them. The registry does not report a multiplicity strategy. Together, these points support a cautious statistical reading: distinguish reported results from recalculations, keep measurement outcomes separate from clinical outcomes, and avoid broader claims not established by the record.

18. Why This Trial Matters Statistically

This study illustrates why a group-mean difference, its confidence interval, and the analysis method need to be considered together. The primary group summaries lead to an unadjusted recalculation whose interval excludes zero, while the sponsor’s regression interval includes zero. Reporting only one p-value would conceal this conflict. The discrepancy makes access to the full model specification and analysis population important for understanding the result.

The registry also labels the design as crossover, while the endpoint summaries present two cord-management groups. A design label can affect how observations should be analyzed, especially if measurements from the same participant are related. Since the sequence and analysis details are not reported, the record shows how a design classification without its operational details can leave readers unable to evaluate the analysis fully.

Optional echocardiography creates another important statistical question: which newborns had a measurement and whether they represent the enrolled population. The record does not give enough information to trace participant flow or assess missingness. This matters because precision calculated from available measurements is not necessarily evidence about all enrolled newborns.

Finally, the secondary outcomes have a generally similar directional pattern, but multiple unadjusted tests do not provide the same evidential strength as a fully specified primary analysis. The case highlights the value of transparent outcome hierarchies, missing-data reporting, analysis-population definitions, and reproducible model descriptions. Those details help distinguish a robust finding from an estimate whose interpretation depends on undocumented choices.

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 registry record leaves several trial-specific interpretive gaps. It classifies the model as crossover but does not report the treatment sequence, periods, whether each participant had measurements under both conditions, or how within-participant dependence was handled. This makes it difficult to determine how the design label relates to the two posted group summaries.

The echocardiogram was optional and dependent on parental consent. The record does not report how many families were approached or consented, how many echocardiograms were completed, whether any were unusable, or why measurements were absent. It also does not define the analysis population or state how missing measurements were handled. As a result, the extent to which the analyzed measurements represent all enrolled newborns cannot be assessed.

The sponsor’s primary regression result differs from the unadjusted recalculation. The record does not provide enough detail about the model, its scale, adjustments, or analysis population to reconcile that difference. The sponsor result takes precedence, but the missing explanation limits independent evaluation. Secondary results are also incomplete: peak systolic velocity is listed as an outcome, but its results are not reported in the registry record. No sponsor analyses are listed for the posted secondary results, and multiplicity handling is not reported.

The registry does not report a clinical-importance threshold for left ventricular output, details of measurement reliability, or later outcomes that could clarify the significance of the echocardiographic findings. Its procedure descriptions are truncated, and it does not identify who was masked. These limitations do not establish that the study methods were deficient; they identify what cannot be assessed from the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Echocardiography Sub-Study of the Umbilical Cord Milking in Non-Vigorous Infants Trial (MINVI) — NCT03798093.
• Registry record last updated 2025-03-25; status last verified 2025-03.
• Results first posted 2025-03-25.
• 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 completed study is the echocardiography sub-study of MINVI, sponsored by Sharp HealthCare. It is classified as randomized, single masked, and crossover. Enrollment is listed as 227, with study start on 2019-01-07 and primary completion on 2021-06-01.

The primary endpoint is mean left ventricular output measured by cardiac ultrasound at 12 ± 6 hours of life. The registry reports group means of 225.0 mL/kg/min for umbilical cord milking and 187.0 mL/kg/min for early cord clamping. The sponsor’s reported regression gives p = 0.08, while an unadjusted recalculation gives p < 0.001 and a different confidence interval. The discrepancy is not explained in the registry record, so the sponsor’s analysis takes precedence.

Three secondary endpoints have posted results; peak systolic velocity results are not reported in the registry record. The record also does not report multiplicity handling, missing-data methods, detailed analysis-population definitions, or the crossover procedures and model details needed to reconcile the primary analyses.