Neonatal Gastro-Esophageal Reflux Disease (GERD) Management Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Neonatal Gastro-Esophageal Reflux Disease (GERD) Management Trial (NCT02486263), a randomized na study. The primary outcome is CLINICAL OUTCOME OF FEEDING SUCCESS.

2. Clinical Question

3. Trial Design

The registry describes a randomized, single-masked, parallel-group trial with enrollment of 76 participants. The two arms were the Study arm, with omeprazole plus restricted feeding volumes, monitored feeding duration, and positioning restrictions, and the Conventional arm, with omeprazole alone and no stated feeding restrictions. The record marks the phase as not applicable and the study status as completed. The listed start is 2012-12, and primary completion is 2020-03-31.

Random allocation means the intended comparison is between groups assigned to different treatment strategies rather than groups formed solely by observed characteristics. A parallel design means participants were assigned to one arm for the comparison, not described as crossing between treatments. The registry identifies the study as single-masked but does not state which people were masked or how masking was implemented. Further details of sequence generation, allocation concealment, adherence, and treatment changes are not reported in the registry record.

The enrollment figure is 76, while the primary outcome denominators are 40 in the Study arm and 36 in the Conventional arm. These are the denominators associated with the reported primary percentages; the record does not explain in detail how participants without an outcome measurement, if any, were handled. Growth and respiratory outcome denominators differ from the primary denominators. The registry does not report a full account of participant flow or analysis populations, so the relationship between enrollment, follow-up, and each analysis cannot be reconstructed from these results alone.

The design compares a combined feeding-management bundle plus medication with medication alone. It cannot, by itself, identify the separate effect of restricted volume, feeding-duration monitoring, or positioning. The original design rationale and the trial's own sample-size assumptions are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

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

Population: The analysis population is the same as the participant assignment.

6. Primary Endpoint

The registry lists the primary outcome as CLINICAL OUTCOME OF FEEDING SUCCESS, measured over Up to 5 weeks after enrollment.

The primary endpoint is the percentage of participants with feeding success up to 5 weeks after enrollment. The registry defines success as achieving full oral feeds, meaning no tube feeds are needed to maintain hydration and nutrition, and/or a decrease of at least 6 points from baseline on the Infant-Gastro-Esophageal Reflux Questionnaire-Revised. The score ranges from 0, indicating no symptoms, to 42, indicating maximum symptoms; a total score greater than or equal to 16 is considered abnormal.

This composite definition captures either a feeding milestone or improvement on a symptom measure. It reflects the trial's focus on feeding difficulty and related symptoms, but the combined endpoint does not show which component accounts for a participant's success. The registry does not report the number meeting each component separately, nor does it state how cases meeting both components were counted beyond the overall definition.

The outcome is reported as a percentage of participants, with a 95% confidence interval for each arm. A percentage summarizes how often the defined event was recorded in each group, while the confidence interval conveys uncertainty around that estimate. The follow-up window is up to 5 weeks after enrollment. The registry record does not report further details about the timing or procedure for assessing the questionnaire or confirming full oral feeds.

7. Results Posted in the Registry

• Conventional: 44.4% (16/36) versus 32.5% (13/40) on control; risk difference 11.9 percentage points (95% CI -9.8 to 33.7), risk ratio 1.37 (0.77–2.43); unadjusted two-proportion z-test p = 0.284.

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.

CLINICAL OUTCOMES: Growth Outcome Measure

• 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:
  • Conventional: mean 26.50 versus 27.60 on control; difference -1.10 (95% CI -5.40 to 3.20), standardized effect d = -0.12; z-test p = 0.616.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Conventional and the control. The interval gives the range of effects that remain compatible with the data.

CLINICAL OUTCOME: Respiratory Outcome Measures

• 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:
  • Conventional: 25.7% (9/35) versus 18.9% (7/37) on control; risk difference 6.8 percentage points (95% CI -12.4 to 26.0), risk ratio 1.36 (0.57–3.25); unadjusted two-proportion z-test p = 0.488.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Conventional and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies growth, development, and respiratory outcomes among the secondary outcomes. Numeric results are posted for growth and respiratory outcomes, but a development result is not reported in the registry record. The secondary findings do not establish a clear and consistent pattern of separation between the treatment strategies. They should be considered alongside, rather than as a substitute for, the primary feeding-success comparison.

The growth result concerns mean weight gain at 5 weeks, while the respiratory result is a participant count at discharge. Those outcomes assess different aspects of health and use different measurement scales. They are not alternative measurements of the primary endpoint, and they do not resolve the uncertainty in feeding success. The registry does not report an integrated analysis combining primary and secondary outcomes, so each result should be interpreted within its own definition and timeframe.

Unadjusted secondary results carry less weight when several outcomes are examined because the chance of finding an apparently noteworthy result by chance can increase across multiple comparisons. The registry does not report a multiplicity adjustment, a hierarchy for testing secondary outcomes, or which outcomes were designated confirmatory. Accordingly, individual secondary p-values should be treated as exploratory unless further analysis-plan information is available. This does not make the measurements irrelevant; it means their evidential strength is limited without a reported strategy for interpreting multiple tests.

The registry lists five outcome measures and reports five analyses, while the posted secondary outcomes include the named growth, development, and respiratory measures. The development outcome data are not reported in the registry record. The record also does not report whether all planned secondary outcomes were collected or why numeric results are unavailable for the development measure. This limits assessment of the full secondary-outcome pattern and the possibility of selective reporting.

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

• CLINICAL OUTCOMES: Growth Outcome Measure
• CLINICAL OUTCOME: Development Outcome Measures
• CLINICAL OUTCOME: Respiratory Outcome Measures

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a chi-squared test for the primary comparison. A chi-squared test assesses whether the observed distribution of a categorical outcome across groups is compatible with no association between group and outcome. For this endpoint, the outcome is classified as feeding success or not, and the result is summarized as a percentage in each arm. The registry's reported test is a superiority analysis, but the record does not give further details about its implementation or any adjustment beyond the named method.

What does a risk difference describe?

A risk difference subtracts the event proportion in one group from the event proportion in the other, with the comparison direction stated explicitly. The recalculated estimate is 0.119 for Conventional compared with Study. A value of zero corresponds to equal proportions; values on either side indicate different directions of the contrast. The confidence interval from -0.098 to 0.337 spans zero, so the data remain compatible with no difference as well as with differences in either direction. The interval is an estimate of uncertainty, not a range containing every possible individual outcome.

How should a p-value be read?

A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The registry reports p = 0.28 for the primary chi-squared test, while the unadjusted recalculation gives p = 0.284. Both are consistent with the confidence interval's inclusion of zero. The registry's own analysis is the reported trial analysis; the recalculation is a separate unadjusted comparison based on the posted summary statistics.

Why report a confidence interval?

A confidence interval expresses the precision of an estimate under the method used to construct it. The arm-specific intervals describe uncertainty in each percentage, and the interval for the risk difference describes uncertainty in the contrast. An interval that includes zero does not prove equality. It indicates that a zero difference is among the values not ruled out by the data and method, while also leaving room for differences in either direction. Wide intervals signal that the estimate is not precise enough to narrow the range of plausible effects substantially.

What does randomization contribute?

Random assignment is intended to make treatment groups comparable, on average, with respect to factors known and unknown at assignment. This supports interpretation of a group contrast as a comparison of the assigned strategies, subject to how allocation, follow-up, adherence, and analysis were handled. The registry identifies randomization but does not report sequence generation, concealment, or the analysis population. Those details are not reported in the registry record and should not be assumed.

Why can binary outcomes be uncertain?

For an outcome recorded as an event or no event, the estimated percentage depends on the number of observed events and the number of participants contributing data. With limited observations, changes in a small number of outcomes can affect the estimated percentages. The reported confidence intervals convey this uncertainty. Statistical significance alone would not determine the importance of the result, and lack of statistical significance is not evidence that the strategies have identical effects.

What is the role of the secondary tests?

The growth outcome is reported as a mean in grams per day with a standard deviation, and the registry names a two-sided t-test. A t-test compares group means, using the variation within the observations to assess uncertainty. The respiratory outcome is a count of participants and is analyzed with a chi-squared test. These outcomes differ in measurement scale and therefore use different summaries and tests. The registry does not report whether assumptions were checked, whether any covariate adjustment was used, or whether the secondary analyses were prespecified.

Why can over-dispersion matter?

As a general statistical point, a model that assumes less variability than the data actually contain can produce uncertainty estimates that are too narrow. Conversely, a model that accounts for extra variability can change standard errors and intervals. The posted primary analysis is a chi-squared test, not a reported count-model analysis, and the registry does not describe an over-dispersion assessment. This concept is relevant generally when outcomes are modeled as counts, but no conclusion about over-dispersion in this trial can be drawn from the registry record.

11. Confidence Intervals and Precision

The primary percentages have 95% confidence intervals of 19% to 49% for the Study arm and 28% to 62% for the Conventional arm. Each interval covers a broad range of possible event percentages, so neither arm's underlying feeding-success rate is estimated with high precision from these data. The overlap between the arm-specific intervals is not itself a formal test of the group difference; the comparison interval is the direct summary of uncertainty for that contrast.

For Conventional compared with Study, the recalculated risk-difference estimate is 0.119, and its 95% confidence interval extends from -0.098 to 0.337. The interval includes zero and spans possible effects in either direction. This means the observed contrast is uncertain: the data do not rule out no difference, nor do they tightly constrain the size or direction of a possible difference. The estimate should not be read as a precise prediction for a future group of infants.

Confidence intervals quantify sampling uncertainty under the method used. They do not automatically account for every source of uncertainty, such as differences in outcome ascertainment, incomplete follow-up, or departures from the analysis plan. Details about those matters are not reported in the registry record. The intervals also do not describe variation in an individual's response; they concern estimates of group-level quantities.

Precision and statistical significance are related but distinct. An interval that includes zero can still contain effects that may matter, while an interval excluding zero would not by itself establish clinical importance. Here, the breadth of the interval is central: the registry results permit a wide range of plausible contrasts, so the point estimate alone should not carry much interpretive weight.

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 illustrations based on observed effects, not the trial's own design calculations. For these non-time-to-event outcomes, the listed figures are participants per arm, not total participants. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The trial's original sample-size assumptions are not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a design intended 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 illustration for a 90% chance. These are design-planning concepts, not guarantees about what a future study would find. The figures do not represent the probability that the trial's conclusion is correct, and they do not indicate the probability that an effect exists.

Each planning row uses a different fraction of the observed effect: 100%, 75%, or 50%. Smaller effects are harder to distinguish from random variation and therefore require more participants for the same target power under otherwise unchanged assumptions. The listed figures can be read as scenarios for planning, rather than as evidence that a particular effect is real or likely to recur. As the assumed effect changes, the required sample size can change substantially.

These figures are not observed power. Observed power is not a useful substitute for interpreting the estimate and its confidence interval after a study is complete. The trial's actual enrollment was 76, and the planning illustrations do not alter the observed outcome data or resolve their uncertainty. The original protocol's justification for enrollment and any planned sample-size revisions are 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 = 0.325; treatment proportion p₁ = 0.444; average p̄ = 0.385.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6881 = 1.3486.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6829 = 0.5747.
4. n = (1.3486 + 0.5747)² / (0.1194)² = 259.3, rounded up to 260 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 <- 0.325                          # control proportion
p1 <- 0.444444444444444                          # 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(2486263)
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 = 260 (80% power), 347 (90% power)
 75% of observed effect: n per arm = 455 (80% power), 609 (90% power)
 50% of observed effect: n per arm = 1,007 (80% power), 1,347 (90% power)
power.prop.test: 259.3 
Simulated power at n = 260 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports a chi-squared primary analysis with p = 0.28. The unadjusted recalculation from the posted arm summaries gives p = 0.284 and a risk-difference confidence interval from -0.098 to 0.337. The recalculation is a simple comparison of the posted summary statistics; it is not a replacement for the trial's reported analysis.

The posted primary result and the recalculation lead to the same broad statistical reading: the data do not establish a clear between-arm difference, and the estimate remains imprecise. The registry reports the sponsor's analysis as the trial analysis, while the recalculated result is useful as a transparent check based on the summary data. The registry does not report additional details about adjustment, analysis population, or the handling of missing outcomes that would permit a fuller comparison of analytic procedures.

For the secondary outcomes with reported analyses, the registry gives p = 0.64 for growth and p = 0.49 for the respiratory outcome. Their unadjusted recalculations give p = 0.616 and p = 0.488, respectively. These are distinct reported and recalculated results, and neither should be presented as if it were the other. The registry does not flag a discrepancy. The sponsor's reported analyses remain the trial's own results; recalculations from summary statistics offer context but cannot reproduce unreported individual-level or adjusted analyses.

15. Multiplicity, Missing Data and Analysis Populations

The registry does not report a plan for controlling multiplicity across the primary and secondary analyses, nor does it describe a testing hierarchy or identify confirmatory and exploratory outcomes. When several outcomes or comparisons are analyzed, unadjusted p-values do not account for the accumulation of statistical tests. As a general statistical principle, this can make isolated secondary findings less persuasive. The primary outcome remains the main endpoint named in the record, but the absence of a reported multiplicity plan limits interpretation of the broader set of results.

The registry does not report how missing outcome data were handled, whether any imputation was used, or whether analyses included all randomized participants. The primary arm denominators are 40 and 36, and the secondary denominators differ, but the record does not provide enough participant-flow detail to determine why those denominators vary. Missing-data methods can affect estimates when outcome availability is related to treatment assignment or participant characteristics; whether that applies is not reported in the registry record.

The analysis population is not reported in the registry record. It is therefore unclear from the posted information whether analyses followed assigned groups regardless of treatment received, included only participants who completed the intervention, or used another definition. The registry identifies randomization, but random assignment alone does not specify the analysis population or establish how participants were handled after randomization.

Interim analyses and stopping rules are not reported in the registry record. Protocol deviations, adherence summaries, and sensitivity analyses are also not reported. These omissions do not imply that such procedures were absent; they mean the registry record does not provide the details needed to assess them. Interpretation is consequently limited to the outcomes and analyses that are reported.

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 records zero serious adverse events in the Study arm, among 40 participants at risk, and zero in the Conventional arm, among 36 participants at risk. It also records zero other adverse events in each arm, with the same respective at-risk denominators, and zero deaths in both arms. These are the posted event counts and should be read as registry entries, not as proof that no adverse event of any kind occurred.

Zero recorded events do not establish that the strategies have identical safety profiles. When no events are recorded, the results still leave uncertainty about the range of event rates compatible with the data, particularly when the number of participants observed is limited. The registry does not report a follow-up window specific to adverse-event collection, definitions for the event categories, or details of how events were solicited and adjudicated. It also does not provide serious-event terms, consistent with no serious events listed in the record.

Safety interpretation is therefore confined to these reported counts and denominators. The figures do not characterize event severity beyond the stated categories, timing, relatedness, or events occurring outside the recorded observation period. No conclusion about comparative safety should be drawn from zero counts alone.

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

The registry reports an observed feeding-success percentage of 33% in the Study arm and 44% in the Conventional arm, with a recalculated risk-difference interval that includes zero. The data do not establish a clear difference between the strategies under the reported comparison. The confidence interval is broad, so the result also does not establish that the strategies have the same effect or exclude potentially meaningful differences in either direction.

The intervention contrast is a feeding bundle plus omeprazole compared with omeprazole alone. The trial therefore speaks to the overall assigned strategies as described, not to the separate contribution of each feeding restriction or monitoring practice. The primary endpoint combines a feeding milestone with symptom-score change, and component-specific results are not reported. It is not possible to identify which component drove the observed event percentages.

The outcome was assessed up to 5 weeks after enrollment. The record does not establish how the result relates to longer-term feeding, development, growth, respiratory health, or family experience. Although growth and respiratory results are also posted, they address distinct outcomes and do not settle the primary comparison. Development results are not reported in the registry record.

These findings are statistical descriptions, not treatment advice. The study record provides limited information about missing data, analysis populations, adherence, and multiplicity, all of which affect how confidently the results can be generalized or interpreted. A non-significant result is not proof of equivalence, and an observed percentage is not a guarantee of what would occur for another group of infants. Any clinical interpretation requires the wider evidence and clinical context, neither of which is established by this registry comparison alone.

18. Why This Trial Matters Statistically

This trial poses a useful statistical question because both arms received omeprazole, while one arm also received a defined feeding-management bundle. That comparison focuses attention on the added bundle rather than contrasting medication with no treatment. At the same time, the bundled design means the individual elements cannot be separated statistically from these results.

The primary endpoint combines a feeding milestone and symptom-score improvement. Such a composite can capture more than one dimension of the trial's clinical question, but it also makes component-specific reporting important. Without separate counts, readers cannot tell which part of the definition accounts for the observed success percentages. Clear endpoint definitions are therefore essential when interpreting a percentage that may represent different paths to success.

The arm estimates and their uncertainty demonstrate why a point estimate alone is insufficient. The observed percentages differ, but the comparison interval spans zero and remains broad. The results illustrate the distinction between an observed direction of effect, statistical evidence for a difference, and precision about the possible size of that difference. These are related questions, but they are not interchangeable.

The registry also shows how complete reporting supports interpretation. Details about missing data, analysis populations, multiplicity, and the development outcome are not reported in the registry record. Their absence limits assessment of the full evidence, even though the reported primary comparison can still be described. For clinical researchers, this is a reminder that outcome definitions, denominators, uncertainty intervals, and analysis-plan details all contribute to an interpretable trial result.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry provides limited detail about the trial methods beyond randomization, single masking, and a parallel design. The method of sequence generation, allocation concealment, identity of masked parties, and procedures for maintaining masking are not reported in the registry record. These details would help readers assess how assignment and outcome assessment may have been protected from bias.

The primary endpoint has two possible routes to success, but the registry does not give component-specific results. The questionnaire score's stated range and abnormal threshold are described, but additional information on assessment timing, assessor training, or the treatment of missing baseline or follow-up scores is not reported. This limits understanding of how the composite outcome was operationalized in practice.

The enrollment count is 76, while denominators vary across the primary and secondary outcomes. Participant flow, withdrawals, reasons for missing measurements, and the analysis population are not reported in the registry record. The registry does not provide adherence or treatment-exposure summaries, so the difference between assigned strategy and treatment received cannot be assessed from these results.

The secondary results are incomplete in the record: a development result is not reported, and no multiplicity strategy is described. Interim analyses, stopping rules, protocol deviations, and sensitivity analyses are also not reported. These are reporting limitations, not evidence that any particular procedure was or was not used. The short primary outcome timeframe, up to 5 weeks after enrollment, also means the registry results do not establish longer-term outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Neonatal Gastro-Esophageal Reflux Disease (GERD) Management Trial — NCT02486263.
• Registry record last updated 2020-07-29; status last verified 2020-07.
• Results first posted 2020-07-29.
• 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

NCT02486263 is the Neonatal Gastro-Esophageal Reflux Disease (GERD) Management Trial, described as a randomized, single-masked, parallel-group study with enrollment of 76 and completed status. It compares omeprazole plus a feeding bundle with omeprazole alone. The primary outcome is feeding success up to 5 weeks after enrollment, defined through full oral feeds and/or improvement on the Infant-Gastro-Esophageal Reflux Questionnaire-Revised.

The registry reports feeding success in 33% of the Study arm and 44% of the Conventional arm. The recalculated risk-difference confidence interval includes zero and is broad, while the registry reports a chi-squared p-value of 0.28. These findings do not establish a clear difference and leave substantial uncertainty about the size and direction of any difference. Growth and respiratory results are posted; a development result is not reported in the registry record. Adverse-event entries show zero recorded serious events, other events, and deaths in either arm. Details about missing data, analysis populations, and multiplicity are not reported.