Physiologic Approach to Sodium Supplementation in Premature Infants: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Physiologic Approach to Sodium Supplementation in Premature Infants (NCT03889197), a randomized phase 4 study. The primary outcome is Change in Somatic Growth (Weight).

2. Clinical Question

The question is about a group-level comparison in a particular trial, not about an individual infant’s expected growth. The posted results give the average change in each randomized group and a reported group-comparison test. A separate unadjusted re-calculation expresses the difference in means and its confidence interval. These summaries address the direction and precision of the observed comparison, but they do not establish the reason for any individual outcome. The record does not report a more detailed eligibility description or the specific population characteristics of participants, so the results cannot be characterized further by subgroup from this record alone.

3. Trial Design

This was a completed, randomized, parallel-group phase 4 trial sponsored by Indiana University. The registry record lists 90 enrolled participants. The recorded study dates are 2019-07-01 for study start and 2023-07-22 for primary completion. The masking description is single; further detail about who was masked is not reported in the registry record.

Participants were assigned to standard of care sodium supplementation or a sodium supplementation algorithm. The control arm followed supplementation as directed by the medical care team. The algorithm arm was described as using spot urine sodium measurements every two weeks, beginning on the 14th -16th postnatal day and continuing until 36 weeks postmenstrual age, with supplementation provided according to the algorithm. The record does not report the specific algorithm thresholds or dosing instructions, so those details cannot be reconstructed from the summary.

The primary outcome was change in somatic growth by weight, recorded as a mean change in z-score with standard deviation. Its measurement period ran from 2 weeks of age to 36 weeks post-menstrual age or transfer from the NICU, whichever occurred first. The reported outcome summaries list 43 participants in each arm. The registry does not explain the relationship between those arm-level outcome counts and the enrollment figure, nor does it report whether any participants were excluded from the primary analysis or why.

The record lists multiple secondary outcome measures, including growth measures at discharge or transfer and respiratory or treatment-related outcomes. There are 14 outcome measures and 14 analyses recorded overall, while 11 secondary outcomes are posted in the summary information. The registry record does not report the original sample-size justification, the planned analysis population, or a detailed statistical analysis plan. In particular, it does not say whether there were interim analyses or how missing outcome data were handled.

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: Of the 385 infants screened for eligibility, 260 met inclusion/exclusion criteria, and 90 provided informed consent.

Overall Study

Reasons for not completing this period:

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 Change in Somatic Growth (Weight), measured over between 2 weeks of age and 36 weeks post-menstrual age or transfer from the NICU (whichever occurs first)..

The primary endpoint is change in somatic growth measured by weight z-score. A z-score places an infant’s weight relative to a population reference, expressed in standard-deviation units. The registry describes a score of 0 as the population mean and a positive score as indicating better growth. The endpoint therefore summarizes change relative to a reference distribution rather than expressing weight in grams.

The recorded interval begins at 2 weeks of age and ends at 36 weeks post-menstrual age or transfer from the NICU, whichever occurs first. This provides a defined period over which the trial compared growth between randomized groups. The use of change focuses the endpoint on how the score moved during that interval, rather than on a single weight measurement at its end. It is a continuous measure, and the posted group summaries are means with standard deviations.

Such a measure is useful for describing growth relative to a population standard, particularly when infants differ in age or size. General statistical interpretation: a group mean condenses the outcomes into one average, while the standard deviation describes the spread of individual values around that average. Neither statistic alone describes every participant’s course. The registry’s endpoint description gives the meaning of the score, but it does not report details about the reference population or how measurements and transfers were handled beyond the stated timeframe.

7. Results Posted in the Registry

• Sodium Supplementation Algorithm: mean 0.16 versus 0.04 on control; difference 0.12 (95% CI -0.10 to 0.34), standardized effect d = 0.23; z-test p = 0.295.

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.

Change in Somatic Growth (Weight) at Discharge/Transfer

• 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:
  • Sodium Supplementation Algorithm: mean 0.24 versus 0.04 on control; difference 0.20 (95% CI -0.13 to 0.53), standardized effect d = 0.26; z-test p = 0.235.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sodium Supplementation Algorithm and the control. The interval gives the range of effects that remain compatible with the data.

Change in Somatic Growth (Length) at Discharge/Transfer

• 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:
  • Sodium Supplementation Algorithm: mean 0.92 versus -0.39 on control; difference 1.31 (95% CI -1.26 to 3.88), standardized effect d = 0.22; z-test p = 0.319.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sodium Supplementation Algorithm and the control. The interval gives the range of effects that remain compatible with the data.

Change in Somatic Growth (Head Circumference) at Discharge/Transfer

• 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:
  • Sodium Supplementation Algorithm: mean 2.07 versus 1.03 on control; difference 1.04 (95% CI -1.19 to 3.27), standardized effect d = 0.20; z-test p = 0.361.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sodium Supplementation Algorithm and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary growth outcomes cover weight, length, and head circumference at discharge or transfer. Their unadjusted comparisons do not provide a consistent basis for a firm claim of a growth difference: estimates vary in scale and are accompanied by uncertainty, and the registry’s reported rank-based tests are not statistically significant at 0.05. Other secondary outcomes address diuretic therapy, mechanical ventilation, supplemental oxygen, and bronchopulmonary dysplasia. Their presence broadens the clinical scope of the results but does not alter the interpretation of the primary endpoint.

Across the secondary endpoints, the record presents a range of growth and clinical measures rather than one unified summary. Secondary results can help describe whether the primary pattern is accompanied by other observations, but they are not substitutes for the prespecified primary question. The primary weight z-score comparison itself was uncertain, and the secondary outcomes do not remove that uncertainty. No single secondary finding should be read as resolving the primary result.

Unadjusted secondary analyses carry less weight when many outcomes are examined because the chance of at least one apparently unusual result increases as the number of comparisons grows. This is a general statistical concern, not a claim that a particular secondary result is false. Adjustment methods can address multiplicity, but the multiplicity strategy is not reported in the registry record. The record lists 14 outcome measures and 14 analyses, while 11 secondary outcomes are posted in the summary information; it does not explain how those counts relate or which outcomes were designated in advance as key secondary outcomes.

Interpretation should therefore emphasize the randomized primary comparison and treat secondary outcomes as supporting, exploratory, or descriptive evidence unless a more detailed analysis plan establishes otherwise. The registry record does not report such a plan or the role assigned to each secondary analysis.

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

• Change in Somatic Growth (Weight) at Discharge/Transfer
• Change in Somatic Growth (Weight) at Discharge/Transfer
• Change in Somatic Growth (Length) at Discharge/Transfer
• Change in Somatic Growth (Head Circumference) at Discharge/Transfer
• Received Diuretic Therapy
• Duration of Mechanical Ventilation
• Need for Supplemental Oxygen at Discharge
• Incidence and Severity of Bronchopulmonary Dysplasia (BPD)

9. Statistical Interpretation

10. Statistical Methods Explained

Two statistical summaries appear for the primary comparison. The sponsor-reported analysis is a Kruskal-Wallis test with p = 0.162. A separate re-calculation treats the endpoint as continuous and compares the arm means: the control mean was 0.04 and the algorithm-arm mean was 0.16. The unadjusted mean difference was 0.12, with a 95% confidence interval from -0.105 to 0.345 and p = 0.295.

What does a mean difference describe?

A mean difference is the average in one group minus the average in another, with the direction depending on which group is subtracted from which. Here, the posted difference is for the algorithm arm relative to control. A positive estimate means the algorithm group’s observed average change was higher; it does not establish that the true group difference is positive. The standard deviations of 0.63 and 0.41 describe the spread of individual weight z-score changes within the two arms. Greater spread generally makes an estimated mean difference less precise when group sizes are held fixed.

Why are there two p-values?

The Kruskal-Wallis test and an unadjusted comparison of means use different statistical approaches. In general, the Kruskal-Wallis test is a rank-based method for comparing distributions across groups, whereas a mean-difference analysis directly targets the difference in averages. Their p-values can differ because the methods rely on different summaries and assumptions. The registry reports the Kruskal-Wallis method for the sponsor analysis; the mean difference and its interval are a simple unadjusted re-calculation from posted summary statistics. The registry does not report enough detail to determine whether the sponsor’s test included additional adjustments or other design features.

A p-value quantifies how unusual data at least as incompatible with a null hypothesis would be if that null model and the test assumptions were correct. It does not tell how large an effect is, whether an effect matters clinically, or the probability that a treatment effect exists. A confidence interval provides a complementary description: it gives a range of values compatible with the data and the method at its stated confidence level. It remains subject to the method’s assumptions and the quality of the underlying data.

Why does variability matter?

General statistical explanation: when individual outcomes vary widely, group averages are less precise unless there is sufficient information to estimate them. The standard deviation is a description of outcome dispersion, not the uncertainty in the estimated mean itself. The standard error describes uncertainty in an estimate; the posted primary re-calculation reports standard errors of 0.096 for control and 0.062 for the algorithm arm. A standard error is not an individual-level spread measure. It is used to quantify how much an estimate would vary across repeated samples under the statistical model.

The outcome is a change score, so the analysis concerns differences in change between groups, not simply the final score or final weight. The registry record does not report whether the analysis adjusted for baseline values, gestational age, or other participant characteristics. It also does not report distributional checks or the handling of any unusual values. No conclusion about those analytic choices can be made from the posted summary.

Why can over-dispersion matter?

General statistical explanation: over-dispersion describes variability greater than a model expects. When it occurs, a model that assumes too little variability can produce standard errors that are too small and confidence intervals that are too narrow. The primary outcome is continuous, and the registry gives standard deviations for the two arms, but it does not characterize over-dispersion or report a model-based variance assessment. No claim that over-dispersion occurred can be made from these summaries. In outcomes with counts or event rates, over-dispersion can also affect inference, but the primary weight endpoint is not a count outcome.

The registry’s primary result is therefore best read alongside both the sponsor-reported rank-based test and the unadjusted estimate of the mean difference. They address the same randomized-group comparison through different methods, and both convey uncertainty rather than a definitive determination of no effect. The record does not report the original statistical analysis plan, multiplicity strategy, or assumptions used to choose the primary analysis. The planning illustration has its own stated assumptions and should not be mistaken for documentation of the trial’s original design.

11. Confidence Intervals and Precision

The primary unadjusted mean difference was 0.12, with a 95% confidence interval from -0.105 to 0.345. A confidence interval describes the range of effect values reasonably compatible with the observed data under the method used. Its inclusion of zero means the data do not rule out no mean difference at the stated confidence level. Because the interval also reaches in both directions, it does not establish a single direction for the underlying difference.

The interval is not a guarantee that the true effect lies within its endpoints, and it does not give the probability that any particular effect is true. Its interpretation depends on the analysis and assumptions. Here, it accompanies a simple unadjusted comparison of means, rather than the sponsor-reported Kruskal-Wallis test. The registry does not report a confidence interval for the sponsor’s test.

Precision is limited by the width of the interval: estimates ranging from -0.105 to 0.345 remain compatible with the posted primary data. The group standard deviations, 0.63 in control and 0.41 in the algorithm arm, show that individual changes varied around their respective averages. The standard errors reported for the means are 0.096 and 0.062. These quantities help explain why an observed difference should not be interpreted without uncertainty.

The interval describes uncertainty in the average comparison, not the range of changes experienced by individual infants. It also does not cover uncertainty arising from unreported analysis choices, missing data, or limits on generalizability. The registry record does not report enough detail to assess those sources fully. The result is consequently more informative as an estimate with substantial uncertainty than as a binary conclusion based only on whether a p-value crosses a threshold.

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 figures are participants per arm for 80% power and participants per arm for 90% power. They are not total events: this is a continuous outcome, and the figures describe participant counts in each of two equally allocated groups. The illustrations use the observed effect or a stated fraction of that effect. For the primary endpoint, planning for 100% of the observed effect gives 308 participants per arm for 80% power and 413 participants per arm for 90% power. Planning for 75% of the observed effect gives 548 participants per arm for 80% power and 733 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,232 participants per arm for 80% power and 1,650 participants per arm for 90% power.

In plain terms, 80% power means that, under the planning assumptions and for the effect being targeted, the design would have an 80% chance of producing a statistically significant result if that effect were the true effect. The 90% column describes a higher chance under the same kind of assumptions. These are planning probabilities for a hypothetical future design, not probabilities that the current trial result is correct. Smaller effects are harder to distinguish from random variation, so the planning figures rise as the assumed effect shrinks.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the target effect is the stated fraction of the observed effect. These figures are planning illustrations, not the trial’s original sample-size justification. The original design assumptions are not reported in the registry record. This is not observed power.

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 = 0.120; pooled standard deviation σ = 0.532.
2. n = 2 × (1.96 + 0.842)² × 0.532² / 0.120² = 308.0, rounded up to 308 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 <- 0.12                      # observed difference in means
sigma <- 0.531507290636733                     # 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(3889197)
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 = 308 (80% power), 413 (90% power)
 75% of observed effect: n per arm = 548 (80% power), 733 (90% power)
 50% of observed effect: n per arm = 1,232 (80% power), 1,650 (90% power)
power.t.test: 308.9 
Simulated power at n = 308 per arm: 0.796 (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 registry reports the sponsor’s primary comparison as a Kruskal-Wallis test with p = 0.162. The separate unadjusted re-calculation compares posted means and gives a mean difference of 0.12, a 95% confidence interval from -0.105 to 0.345, and p = 0.295. The re-calculation is a summary-statistic comparison and does not replace the sponsor’s reported analysis.

The results are not marked as discrepant in the registry summary. The two p-values need not match because the methods differ: one is rank-based, while the re-calculation targets the mean difference. The sponsor’s analysis is the analysis reported by the trial record; the re-calculated estimate offers a complementary description of the mean contrast and its precision. The registry does not report enough detail to determine whether the sponsor’s method included adjustments not represented in the re-calculation.

Neither result is below 0.05, the significance level used in the planning illustration. Both should be interpreted as evidence that does not establish a clear difference, rather than proof of identical outcomes. The confidence interval is available for the re-calculated mean difference, while no interval is reported for the sponsor’s Kruskal-Wallis result. The distinction between the analyses matters when interpreting the magnitude and uncertainty of the comparison.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 14 outcome measures and 14 analyses, and the summary information identifies 11 posted secondary outcomes. The record does not explain the difference between these counts or report a multiplicity adjustment strategy. When many outcomes are tested, some results can appear notable by chance even if there are no underlying differences. General statistical methods for addressing this include adjusting significance thresholds or controlling an error rate across a defined family of comparisons. Whether either approach was planned or used is not reported in the registry record.

Missing-data handling is also not reported. The primary outcome summaries list 43 participants per arm, while overall enrollment is 90. The registry record does not describe why those numbers differ, whether all enrolled participants were randomized, whether every randomized participant contributed to the endpoint, or how unavailable measurements were treated. The counts alone cannot establish that data were missing or identify any reasons for a difference between enrollment and outcome summaries.

The analysis population is not reported in the registry record. It is therefore not possible from the posted information to determine whether the primary analysis followed an intention-to-treat principle, included only participants with observed outcomes, or used another population definition. The record also does not describe imputation, sensitivity analyses, exclusions, or the handling of transfers before the endpoint’s stated assessment time.

These omissions affect how confidently the posted estimates can be generalized to all randomized participants. They do not invalidate the reported summaries, but they limit assessment of possible bias from missing outcomes and analytic choices. The registry record also does not report interim analyses or a detailed statistical analysis plan, so the timing and governance of the analyses cannot be assessed from this information.

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: hyponatremia (4.7%), edema/anasarca (2.3%), acute kidney injury (2.3%), seizure (2.3%), bacteremia (2.3%).

The serious adverse event summaries report 3 affected participants among 43 at risk in the control arm and 2 among 43 at risk in the sodium supplementation algorithm arm. The record reports zero deaths in each arm. These are participant counts, not event rates adjusted for follow-up time, and the registry summary does not explain the seriousness criteria or the duration over which participants were monitored.

The record also lists other, non-serious adverse events in 5 of 43 control participants and 9 of 43 algorithm-arm participants. Serious-event terms appearing in the record include Hyponatremia at 4.7%, Edema/Anasarca at 2.3%, Acute kidney injury at 2.3%, Seizure at 2.3%, bacteremia at 2.3%, and Pneumonia at 2.3%. These listed terms should be read as the registry’s reported event information; the summary does not establish that each event was caused by the intervention. The record does not provide further detail about event timing, recurrence, severity grading, or attribution.

Adverse-event counts in a trial of this size can describe what was reported in the enrolled groups, but they do not by themselves determine comparative risk. Differences in counts may be imprecise, and the posted summary does not provide a statistical comparison or confidence intervals for these safety outcomes. The zero deaths recorded in both arms is a description of this trial’s reports, not evidence about mortality risk beyond the observed study participants and follow-up.

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

The primary result is an estimated mean difference in change in weight z-score of 0.12 for the algorithm arm relative to control. The 95% confidence interval, from -0.105 to 0.345, includes zero and spans values in both directions. The sponsor-reported Kruskal-Wallis test has p = 0.162, while the unadjusted mean comparison has p = 0.295. Together, these summaries do not establish a clear statistical difference in the primary outcome.

That conclusion does not mean the groups had identical outcomes. A failure to show a clear difference is not a demonstration of equivalence, and the interval leaves uncertainty about the magnitude and direction of the underlying mean comparison. Nor does the point estimate alone establish that the algorithm improves growth. The inference is limited to the outcome, groups, and timeframe described in the registry.

The result also does not answer every question about sodium supplementation. The registry describes an algorithm that used repeated spot urine sodium measurements, but the primary endpoint is change in weight z-score, not a direct measure of sodium balance or the success of each individual supplementation decision. Secondary growth and clinical outcomes add context, but their interpretation is affected by multiple comparisons and incomplete detail about the analysis plan.

General statistical interpretation: an estimate, its uncertainty interval, and the design context should be read together. A p-value alone cannot establish clinical importance, exclude meaningful effects, or assign causation to an individual outcome. Randomization supports a group comparison, but conclusions still depend on how outcomes were measured, which participants were analyzed, and how missing data and multiplicity were handled. Those details are not reported in the registry record.

The record therefore supports a cautious description: the observed average change was higher in the algorithm arm, but the uncertainty is broad enough that the comparison does not provide a definitive directional conclusion. It does not establish that the algorithm is effective or ineffective, and it should not be used as individual medical guidance.

18. Why This Trial Matters Statistically

This trial raises a useful statistical question about how a biologically guided intervention is evaluated. The algorithm used repeated spot urine sodium measurements to guide supplementation, while the primary endpoint assessed change in weight relative to a population standard. Linking an intervention process to a broader growth outcome creates a clear group-comparison question, but interpretation still depends on the precision of that outcome and on how the analysis was conducted.

The primary result illustrates why effect estimates and confidence intervals are more informative than a binary reading of statistical significance alone. The estimated mean difference was 0.12, but its 95% confidence interval ranged from -0.105 to 0.345. That interval communicates uncertainty about both direction and magnitude. The sponsor’s rank-based test and the unadjusted mean comparison also show that method choice matters: different valid summaries can emphasize different features of the observed data.

The study is also a reminder that a posted enrollment number does not by itself reveal how much information contributed to a particular endpoint. The registry reports 90 enrolled participants and outcome summaries for 43 participants per arm, but does not explain the relationship between those counts. Reporting the analysis population, missing-data approach, and original design assumptions would help readers assess precision and risk of bias.

Finally, the registry includes multiple secondary outcomes, for which multiplicity is relevant. Without a reported analysis plan, readers cannot readily distinguish confirmatory outcomes from exploratory ones or know whether adjustments were applied. These issues are common in clinical-trial interpretation and are especially important when the primary comparison is uncertain and multiple related outcomes are available.

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 trial-specific limitations follow directly from what is not reported. The registry record does not provide a detailed eligibility description or baseline characteristics, so it is difficult to judge how closely the participants represented the wider population of premature infants. The primary population field is blank. The record also does not give the specific algorithm thresholds or dosing instructions, which limits independent understanding of how urine sodium measurements translated into supplementation.

The primary summaries list 43 participants per arm despite an enrollment of 90, and the record does not explain the difference. It does not identify the analysis population, exclusions, or approach to missing outcomes. The outcome timeframe ends at 36 weeks post-menstrual age or NICU transfer, whichever occurs first; the record does not describe how transfer timing affected measurement or analysis.

The posted comparison includes a sponsor-reported Kruskal-Wallis test and an unadjusted re-calculation of a mean difference. A detailed statistical analysis plan, baseline-adjustment approach, distributional assessments, and handling of unusual values are not reported. The registry also does not report a multiplicity strategy despite multiple outcomes and analyses, nor does it describe interim analyses or the original sample-size rationale.

Safety reporting is limited to group counts and listed serious-event terms. Follow-up duration for adverse events, event attribution, and detailed severity information are not reported in the registry record. These limitations do not negate the posted results, but they constrain the ability to assess bias, reproducibility, and how far the findings apply beyond this trial.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Physiologic Approach to Sodium Supplementation in Premature Infants — NCT03889197.
• Registry record last updated 2024-11-22; status last verified 2024-08.
• Results first posted 2024-11-22.
• 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

NCT03889197, titled Physiologic Approach to Sodium Supplementation in Premature Infants, is recorded as a completed, randomized, single-masked, parallel-group phase 4 trial sponsored by Indiana University. Enrollment was 90. The study compared standard of care sodium supplementation with a urine-sodium-guided supplementation algorithm.

The primary endpoint was change in weight z-score from 2 weeks of age to 36 weeks post-menstrual age or NICU transfer, whichever occurred first. Mean change was 0.04 in control and 0.16 in the algorithm arm. The unadjusted mean difference was 0.12, with a 95% confidence interval from -0.105 to 0.345; the sponsor-reported Kruskal-Wallis test gave p = 0.162.

The posted primary comparison does not establish a clear difference and remains imprecise. Important details about the analysis population, missing data, multiplicity, and the original sample-size justification are not reported in the registry record.