Aerosolized Surfactant in Neonatal RDS: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Aerosolized Surfactant in Neonatal RDS (NCT02294630), a randomized phase 1, phase 2 study. The primary outcome is Number of Participants With Adverse Events as a Measure of Safety and Feasibility.

2. Clinical Question

The clinical rationale in the registry is that surfactant deficiency causes respiratory distress syndrome, while intratracheal surfactant delivery requires intubation and mechanical ventilation. Aerosol delivery during noninvasive ventilation was proposed as an alternative route. The registry’s stated overall hypothesis concerned safety and feasibility and possible short-term improvement in oxygenation and ventilation; the posted outcomes and comparisons should be read as trial results, not as proof of that hypothesis.

3. Trial Design

The registry describes a randomized, parallel-group, unblinded Phase I/II study. Its brief summary identifies the proposed study as a single-center randomized trial. The registry lists an enrollment of 159 and a completed status. The recorded study period began in 2014-12, with primary completion in 2019-07. These dates describe the registry record and do not add information about the conduct of individual visits or follow-up.

Four aerosolized surfactant schedules were compared. Dose Schedule I was 100 mg phospholipid/kg at a 1:1 dilution; Dose Schedule II used the same dose at a 1:2 dilution. Dose Schedule III was 200 mg phospholipid/kg at a 1:1 dilution; Dose Schedule IV used that dose at a 1:2 dilution. Thus, the schedules varied in dose, dilution, or both. The posted arm counts were 37 for Schedule I, 38 for Schedule II, 35 for Schedule III, and 39 for Schedule IV.

Comparisons in the posted results use Schedule I as the reference. This is an active schedule comparison: all four groups are described as receiving aerosolized surfactant, and the registry record does not show a separate untreated or usual-care group in these arms. The lack of masking is relevant when interpreting outcomes that may depend on observation or reporting. The record does not report the randomization sequence, allocation concealment, or procedures used to maintain treatment assignment.

The primary outcome concerns adverse events over the treatment period and a short interval afterward. Secondary measures include blood gas parameters and pulse oximetry measured 60±30 minutes after the end of study intervention, along with other listed clinical measures. The registry record does not report the trial’s original sample-size justification or a detailed protocol for 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: Of 159 enrolled and randomized participants, 149 met eligibility criteria and proceeded with treatment.

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.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Adverse Events as a Measure of Safety and Feasibility, measured over During and within 6 hours after end of study drug administration, expected maximum of approximately 14 hours.

The primary endpoint is the number of participants with adverse events as a measure of safety and feasibility. The registry specifies the observation window as during study-drug administration and within 6 hours after its end, with an expected maximum of approximately 14 hours. The outcome description singles out surfactant reflux because it was considered one of the most likely adverse events associated with the intervention.

Counting participants with an event gives a direct description of how often an adverse event was recorded in each schedule group. It is distinct from counting the total number of events: a participant with more than one event would still be counted once for a participant-based outcome, according to the endpoint title. The registry does not provide further operational detail on how multiple events, severity, or event attribution were handled for this primary measure.

This endpoint is used to characterize immediate safety and feasibility in the context of aerosolized surfactant administration. Its short observation window means it addresses events during treatment and soon afterward, rather than longer-term safety. The posted counts were 3 participants for Schedule I, 8 for Schedule II, 4 for Schedule III, and 12 for Schedule IV. These counts describe the groups in the registry record; they do not by themselves establish that schedule caused any difference. The comparisons and their uncertainty are needed to assess how compatible the observed pattern is with a range of underlying differences.

7. Results Posted in the Registry

• Dose Schedule II: 21.1% (8/38) versus 8.1% (3/37) on control; risk difference 12.9 percentage points (95% CI -2.7 to 28.6), risk ratio 2.60 (0.75–9.04); unadjusted two-proportion z-test p = 0.113.
• Dose Schedule III: 11.4% (4/35) versus 8.1% (3/37) on control; risk difference 3.3 percentage points (95% CI -10.4 to 17.0), risk ratio 1.41 (0.34–5.85); unadjusted two-proportion z-test p = 0.635.
• Dose Schedule IV: 30.8% (12/39) versus 8.1% (3/37) on control; risk difference 22.7 percentage points (95% CI 5.7 to 39.6), risk ratio 3.79 (1.16–12.38); unadjusted two-proportion z-test p = 0.013.

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.

Blood Gas Parameters - pH

• 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:
  • Dose Schedule II: mean 7.36 versus 7.35 on control; difference 0.01 (95% CI -0.02 to 0.04), standardized effect d = 0.16; z-test p = 0.476.
  • Dose Schedule III: mean 7.36 versus 7.35 on control; difference 0.01 (95% CI -0.02 to 0.04), standardized effect d = 0.18; z-test p = 0.448.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dose Schedule II and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dose Schedule III and the control. The interval gives the range of effects that remain compatible with the data.

Blood Gas Parameters - pCO2

• 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:
  • Dose Schedule II: mean 45.00 versus 45.00 on control; difference 0.00 (95% CI -3.85 to 3.85), standardized effect d = 0.00; z-test p = 1.000.
  • Dose Schedule III: mean 43.00 versus 45.00 on control; difference -2.00 (95% CI -5.26 to 1.26), standardized effect d = -0.28; z-test p = 0.229.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dose Schedule II and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dose Schedule III and the control. The interval gives the range of effects that remain compatible with the data.

Pulse Oximetry

• 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:
  • Dose Schedule II: mean 96.95 versus 95.95 on control; difference 1.00 (95% CI -0.98 to 2.98), standardized effect d = 0.23; z-test p = 0.322.
  • Dose Schedule III: mean 97.37 versus 95.95 on control; difference 1.42 (95% CI -0.08 to 2.92), standardized effect d = 0.44; z-test p = 0.064.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dose Schedule II and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dose Schedule III and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results cover short-term physiological measures, including blood gas parameters and pulse oximetry measured 60±30 minutes after the end of the intervention. Across the reported comparisons, the mean values are broadly similar, with some numerical differences between schedules. The intervals for the posted mean differences include no difference, so these results do not provide precise evidence of separation between the compared schedules at that assessment time.

These secondary measures relate to the primary result by adding a limited picture of immediate physiology alongside acute adverse-event counts. They do not directly validate or explain the event-count pattern, and they are not substitutes for the primary safety and feasibility outcome. Nor do short-term measurements establish longer-term clinical outcomes. The registry lists additional secondary measures, including vital signs, surfactant dose counts, and air-leak outcomes; detailed results for every listed measure are not described in the summaries.

The secondary comparisons carry less weight than a single prespecified primary analysis when the analysis plan and multiplicity approach are not reported. Many outcomes and comparisons create more opportunities for an apparently noteworthy result to arise by chance. The registry record does not state how such multiplicity was handled. The secondary findings are therefore best treated as descriptive or exploratory, with attention to their estimates and uncertainty rather than to isolated p-values.

Differences in denominators across secondary outcomes also matter. The posted number of observations is not identical for every measure, and the registry record does not explain all outcome-specific missingness or analysis populations. Consequently, comparisons across different outcomes should not be interpreted as if they necessarily came from the same set of participants.

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

• Blood Gas Parameters - pH
• Blood Gas Parameters - pCO2
• Pulse Oximetry
• Vital Signs - Heart Rate
• Vital Signs - Respiratory Rate
• Vital Signs - Systolic Blood Pressure
• Number of Doses of Surfactant - Aerosolized & Intratracheal
• Pneumothorax, Pneumomediastinum or Other Air Leak

9. Statistical Interpretation

10. Statistical Methods Explained

The posted binary outcome is the number of participants with an event. For each schedule, the event count is interpreted against the number of participants in that group. A risk is the proportion of participants who experienced the event. A risk difference compares two such proportions by subtraction. A positive risk difference means the event proportion was higher in the schedule named in the comparison than in Schedule I; a negative one would mean it was lower. These comparisons are unadjusted in the posted calculations.

A confidence interval describes a range of values that are reasonably compatible with the data under the statistical model. For a risk difference, zero represents no difference in the underlying event proportions. An interval crossing zero indicates that the observed data do not rule out no difference at the interval’s stated confidence level. An interval entirely on one side of zero indicates that the compatible differences lie on that side, while still allowing a range of effect sizes. Confidence intervals do not give the probability that a specific value is true, and they do not address bias or unmeasured limitations in study conduct.

The p-value is another summary of compatibility with a null hypothesis of no difference, under the assumptions of the test. A smaller p-value means the observed data, or data more extreme, would be less compatible with that null hypothesis. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The registry record does not report whether the displayed primary comparisons were the sponsor’s prespecified inferential tests, nor does it report a detailed primary analysis plan.

For continuous outcomes, the posted comparisons use mean differences. A mean difference compares the group averages in the outcome’s original units. The associated standard deviations describe variation among individual measurements; they are not confidence intervals for the group means. For these outcomes, zero mean difference corresponds to equal averages. A confidence interval crossing zero leaves no difference among the compatible possibilities at its stated confidence level.

General statistical context: a standard deviation describes spread among measurements, whereas a standard error describes uncertainty in an estimated quantity such as a mean. The standard error generally becomes smaller with more information, but it also depends on the variability in the observations. A confidence interval is formed from an estimate and its uncertainty, with a procedure that reflects assumptions about the data and analysis. The registry record does not detail the exact procedures behind every reported summary, so interpretation should stay with the posted estimates and intervals rather than infer additional modeling choices.

Random allocation is intended to make groups comparable in expectation, reducing systematic differences in baseline factors. It does not guarantee identical groups in a particular trial, and it cannot correct errors in measurement, missing outcomes, or departures from the allocation plan. The registry record identifies the study as randomized but does not report the sequence-generation method, concealment procedures, baseline balance, or how adherence to assigned schedules was handled in analysis.

The study was unblinded. In general, lack of masking can matter when outcome assessment or reporting involves judgment, because expectations can influence what is observed or recorded. Participant counts for adverse events may be more direct than subjective scales, but definitions, attribution, and ascertainment still matter. The registry record does not describe event adjudication or whether assessors were independent of treatment delivery.

The posted comparisons are relative to Schedule I, rather than all possible pairwise comparisons among schedules. The record gives several schedule comparisons for the primary outcome and multiple secondary measures. General statistical context: when many hypotheses are examined, the chance of at least one apparently unusual result can increase if each test is judged separately without accounting for multiplicity. The registry record does not report a multiplicity strategy, so the unadjusted p-values should be viewed as exploratory evidence rather than as a complete family-wise assessment.

The primary outcome is binary at participant level; it does not have a continuous distribution. The secondary blood gas and pulse-oximetry outcomes are reported as means and standard deviations. The record does not report missing-data methods, analysis populations, or a detailed account of participants excluded from a particular outcome analysis. Some arm-specific outcome counts differ across measures, so outcome-specific denominators should be taken from each posted result rather than assumed to be identical.

General context: over-dispersion occurs when the variability in data exceeds what a simple model assumes. It can make standard errors too small if not accommodated. The registry record does not identify a model for over-dispersion, and the posted endpoint is a participant count rather than a repeated event-rate measure. No inference about such a model should be made from the counts alone.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an estimated difference. The primary comparisons include confidence intervals for the risk difference between each schedule and Schedule I. Schedule II and Schedule III intervals include no difference, leaving both no difference and differences in either direction among the compatible possibilities. The interval for Schedule IV is entirely above no difference. That interval supports a positive estimated difference in the unadjusted comparison, but it still spans multiple possible magnitudes. An interval’s direction and width should be considered together: a directional result can still leave uncertainty about the size of the difference.

The observed primary counts are based on groups with 35 to 39 participants each. Counts of events are limited, so a small change in the number of participants with an event can materially affect the estimated proportion. This helps explain why estimates from these groups should be read cautiously, even when an interval excludes zero. A confidence interval expresses sampling uncertainty under its analysis assumptions; it does not include uncertainty from unreported aspects of conduct, measurement, or generalizability.

The secondary comparisons also show uncertainty. The posted intervals for the pH, pCO2, and pulse-oximetry mean differences include zero. Their estimates therefore do not precisely distinguish a difference from no difference in the posted comparisons. Some intervals are narrower than others, reflecting differences in the observed variability and information available for those measures. The registry record does not report a prespecified threshold for a clinically important difference, so statistical precision cannot be translated into a judgment about clinical importance from these results alone.

Precision is not the same as reliability or absence of bias. A narrow interval can still be misleading if the underlying analysis is biased, and a wide interval can arise even in a well-conducted study when information is limited. Here, the acute observation window, unblinded design, modest arm sizes, and unreported analysis details all matter alongside the statistical intervals.

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, not total events. The outcomes used for these planning illustrations are not time-to-event outcomes. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to be detected is set to the stated fraction of the observed effect for the relevant comparison. The registry record’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column represents the number of participants per arm that the planning calculation estimates would give an 80% chance of detecting the specified effect under the stated assumptions. The 90% power column uses a higher probability of detection, and therefore generally calls for more participants per arm for the same assumed effect. These are planning quantities: they are not observed power.

Rows for planning at 100%, 75%, and 50% of the observed effect illustrate how the assumed effect size changes the required sample. Smaller effects are harder to distinguish from random variation, so the planning calculation requires more participants per arm to detect them at the same power level. This is a general relationship, not evidence that a future study will achieve the assumed effect.

The observed effects in a small study can be unstable, especially when event counts are limited. Using an observed effect as a planning input can therefore produce optimistic or otherwise uncertain sample-size illustrations. The figures do not incorporate any unreported considerations such as attrition, multiple comparisons, or a clinically important target effect. They are not a reconstruction of the trial’s original design rationale and should not be treated as a recommended enrollment target without a separate design assessment.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.081; treatment proportion p₁ = 0.211; average p̄ = 0.146.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4991 = 0.9782.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4906 = 0.4129.
4. n = (0.9782 + 0.4129)² / (0.1294)² = 115.5, rounded up to 116 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 <- 0.0810810810810811                          # control proportion
p1 <- 0.210526315789474                          # 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(2294630)
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 = 116 (80% power), 155 (90% power)
 75% of observed effect: n per arm = 187 (80% power), 250 (90% power)
 50% of observed effect: n per arm = 376 (80% power), 503 (90% power)
power.prop.test: 115.5 
Simulated power at n = 116 per arm: 0.810 (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. Multiplicity, Missing Data and Analysis Populations

The registry record identifies multiple schedules, a primary safety and feasibility outcome, and numerous secondary outcomes. The posted primary comparisons each use Schedule I as the reference. The record does not report whether the comparisons were prespecified in this form, whether any were designated as confirmatory, or whether a statistical procedure was used to control multiplicity. Without that information, unadjusted p-values should not be treated as if they account for all the comparisons made.

Multiplicity matters because repeated testing can increase the chance of at least one result appearing unusual under a collection of null hypotheses. This general issue does not mean that an individual finding is false; it means that its evidential weight depends partly on the analysis plan and the full set of tests. The registry record does not report interim analyses or stopping rules, so no claim about their use can be made.

Missing-data handling and analysis populations are also not reported in the registry record. The record does not specify whether the primary outcome was analyzed in all randomized participants, only those who received intervention, or another defined population. It does not explain how missing outcome observations were treated, whether there were withdrawals, or whether participants were analyzed according to assigned schedule. These details affect how well the posted estimates preserve the benefits of randomization and how representative the outcome summaries are.

Outcome-specific counts vary among some secondary measures. That variation may reflect differing availability of measurements, but the registry record does not explain the reason. It is therefore not possible to determine from these results alone whether missingness was related to schedule, clinical status, or another factor. The observed summaries remain useful descriptions of what was posted, while uncertainty about the analysis populations limits stronger interpretation.

15. 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 non-serious adverse event terms

The serious adverse-event figures show zero affected participants in each of the four dose schedules. The at-risk counts were 37 for Schedule I, 38 for Schedule II, 35 for Schedule III, and 39 for Schedule IV. The registry also reports zero deaths in each schedule. These are observed counts in the registry record, not proof that serious adverse events cannot occur.

A zero count in a group means no serious adverse event was recorded among the participants included in that group’s reported safety count. It does not establish that the underlying risk is zero, particularly when group sizes are limited. The registry record does not provide confidence intervals for these serious-event counts or a detailed definition of the serious adverse events included.

The primary endpoint is broader than the serious adverse-event listing: it counts participants with adverse events in the acute treatment window, and its description highlights surfactant reflux. Thus, zero serious events should not be read as zero adverse events. The registry reports other adverse-event counts separately, but the serious-event figures alone do not characterize the overall burden or severity of all events.

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

The posted primary results describe different observed acute adverse-event counts across four aerosolized surfactant schedules. The unadjusted comparison between Schedule IV and Schedule I has a p-value of 0.013 and a confidence interval for the risk difference that lies above no difference. The comparisons for Schedules II and III have intervals that include no difference. This pattern is evidence about the recorded outcomes in this trial, with uncertainty, rather than a complete answer about comparative safety.

The findings do not establish that any schedule is clinically preferable. The registry record does not provide a threshold for a clinically important difference, nor does the primary endpoint measure longer-term outcomes. The groups received different dose and dilution combinations, so the results should not be generalized to a different formulation, delivery method, or population based on these data alone.

The trial also does not compare aerosolized surfactant with no surfactant or a non-aerosolized treatment in the posted arms. It therefore cannot, from these comparisons, establish the relative effect of aerosol delivery versus other approaches. Its brief summary sets out a rationale and hypothesis involving noninvasive ventilation, safety, feasibility, and short-term physiological change. The observed comparisons do not by themselves confirm all parts of that hypothesis.

The secondary results add limited short-term physiological information. They should not be taken as evidence about later respiratory outcomes or longer-term health. The absence of reported serious adverse events is reassuring as an observation in these groups, but it does not demonstrate absence of risk. The study is most appropriately understood as a randomized early-phase comparison that contributes estimates and feasibility-related information, while leaving important questions for additional evidence.

17. Why This Trial Matters Statistically

This trial is statistically informative because it compares several dose and dilution schedules within a randomized design, rather than presenting a single uncontrolled group. That structure allows direct estimation of differences between schedules, with Schedule I as the posted reference. It also illustrates why the result depends on the comparison being asked: the pattern for Schedule IV differs from the pattern for Schedules II and III.

The study highlights the importance of pairing event counts with uncertainty. The primary outcome counts are straightforward to understand, but relatively limited group sizes and event numbers leave the precision of the estimated differences important. A p-value alone cannot communicate the range of compatible effects, while a confidence interval cannot resolve questions about unreported analysis procedures or clinical importance.

It also demonstrates the role of endpoints and time windows in interpretation. The primary measure captures acute adverse events during and soon after administration; it does not represent a comprehensive assessment of later safety or effectiveness. The physiological secondary measures are snapshots taken shortly after intervention. Statistical interpretation must follow those defined outcomes rather than extend them to outcomes the registry does not report.

Finally, the trial underscores why an early-phase study’s estimates may be useful for planning yet insufficient as a definitive basis for broad conclusions. Planning figures depend on assumptions about effect size and design, and they are distinct from the study’s original sample-size rationale, which is not reported in the registry record. Clear reporting of multiplicity, missing data, analysis populations, and randomization procedures would help readers assess the strength and scope of the findings.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations specific to this trial constrain interpretation. It is described as a single-center, unblinded Phase I/II study. Results from one center may not capture variation in practice or populations across other settings, and unblinded care may influence event ascertainment or reporting. The registry record does not describe independent event adjudication, so the degree to which outcome assessment was insulated from treatment knowledge is not reported.

The primary outcome covers a short period during and after administration. It can characterize acute events but does not address longer-term safety. The secondary blood gas and pulse-oximetry measures were collected around 60±30 minutes after intervention, which is also a short-term assessment. The record does not provide longer-term outcome results in the registry record for this analysis.

The four schedules differ in dose and dilution, which makes the observed comparisons useful for the regimens as a whole but does not isolate a single factor across every comparison. The posted results use Schedule I as the reference, and not every possible pairwise contrast is reported for every secondary measure. No no-surfactant or usual-care arm is described among the posted groups.

Group sizes are modest, and some event counts are small. This limits precision, especially for uncommon outcomes. The registry record does not report the original sample-size justification, detailed randomization procedures, missing-data approach, analysis populations, or multiplicity plan. These reporting gaps prevent assessment of important features of the planned and performed analyses. Outcome-specific denominators also vary, without an explanation in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Aerosolized Surfactant in Neonatal RDS — NCT02294630.
• Registry record last updated 2021-08-25; status last verified 2021-07.
• Results first posted 2021-08-25.
• 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.

22. Record Summary

The registry record describes NCT02294630, Aerosolized Surfactant in Neonatal RDS, as a completed randomized, unblinded, parallel Phase I/II study. It lists enrollment of 159 and identifies preterm neonates with respiratory distress syndrome as the study population. Four aerosolized surfactant schedules varied by dose and dilution.

The primary measure was the number of participants with adverse events during administration and within 6 hours after its end, with an expected maximum window of approximately 14 hours. Posted counts were 3, 8, 4, and 12 for Schedules I through IV. The unadjusted Schedule IV comparison with Schedule I had a p-value of 0.013; the other two posted comparisons had p-values of 0.113 and 0.635.

Short-term physiological outcomes were also posted. The registry record does not report several details needed for fuller assessment, including the original sample-size justification, multiplicity approach, missing-data methods, and analysis populations. The results describe the posted comparisons and should be interpreted within those limits.