Surfactant Via Endotracheal Tube vs. Laryngeal Mask Airway (LMA) in Preterm Neonates With Respiratory Distress Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Surfactant Via Endotracheal Tube vs. Laryngeal Mask Airway (LMA) in Preterm Neonates With Respiratory Distress Syndrome (NCT02164734), a randomized phase 4 study. The primary outcome is Number of Participants Failing to Avoid Invasive Mechanical Ventilation.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group, open-label Phase 4 trial sponsored by Albany Medical College. Enrollment is recorded as 93, and the study status is terminated. The registry lists a start date of 2014-06 and primary completion on 2020-05-20. It does not report why the trial was terminated, so the status alone does not explain whether termination was related to recruitment, safety, study conduct, or another reason.

The study compared two approaches to rescue surfactant delivery in preterm neonates with respiratory distress syndrome. In the endotracheal-intubation group, surfactant was given through an endotracheal tube after remifentanil and atropine pre-medication. In the laryngeal-mask group, surfactant was given through a laryngeal mask airway after atropine pre-medication. The stated intention was to remove the airway after surfactant administration and return the infants to non-invasive CPAP support.

Randomization is reported, but the method used to generate the allocation sequence, conceal assignments, or manage the allocation process is not reported in the registry record. Masking is listed as none. The record therefore describes an unmasked comparison; it does not report whether outcome assessment was independently blinded.

The posted primary outcome groups contain 42 participants in the endotracheal-intubation group and 51 in the laryngeal-mask group. These are the group counts reported with the results, not an explanation of the trial's recruitment target or original design. The trial's original sample-size assumptions and justification 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

Analysis population for the primary outcome, as defined in the registry: Analysis by intention-to-treat

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: Intention-to-treat analysis

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Failing to Avoid Invasive Mechanical Ventilation, measured over 120 hours.

The primary endpoint counts participants who failed to avoid invasive mechanical ventilation within 120 hours. The registry also includes specified clinically equivalent outcomes: FiO2 > 0.60 to maintain the target SpO2, a second surfactant dose within 8 hours, or more than 2 total surfactant doses. The outcome is therefore broader than ventilation alone; it combines the principal clinical concern with treatment-related criteria defined as failure in the registry.

This endpoint addresses the trial's stated objective of reducing the need for endotracheal intubation and mechanical ventilation while achieving comparable surfactant treatment efficacy. Counting participants with an event makes the outcome binary for each participant: a participant either meets the failure definition or does not. The posted primary result is a count in each randomized group, with the analysis identified as intention-to-treat.

Using a defined observation window and explicit failure criteria makes the outcome interpretable across the two delivery approaches. It also means that the result should be understood as the frequency of the registry's composite failure definition, rather than as a direct measure of ventilation alone. The registry record does not provide a separate primary result for each component of that definition, so the contribution of ventilation, oxygen requirement, and repeat surfactant criteria cannot be distinguished from the posted primary count.

7. Results Posted in the Registry

• Laryngeal Mask Airway: 19.6% (10/51) versus 28.6% (12/42) on control; risk difference -9.0 percentage points (95% CI -26.4 to 8.5), risk ratio 0.69 (0.33–1.43); unadjusted two-proportion z-test p = 0.311.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number of Surfactant Doses

• 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:
  • Laryngeal Mask Airway: mean 1.60 versus 1.60 on control; difference 0.00 (95% CI -0.30 to 0.30), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Laryngeal Mask Airway and the control. The interval gives the range of effects that remain compatible with the data.

Rate of Pneumothorax

• 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:
  • Laryngeal Mask Airway: 11.8% (6/51) versus 11.9% (5/42) on control; risk difference -0.1 percentage points (95% CI -13.3 to 13.1), risk ratio 0.99 (0.32–3.01); unadjusted two-proportion z-test p = 0.983.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Laryngeal Mask Airway and the control. The interval gives the range of effects that remain compatible with the data.

Rate of Bronchopulmonary Dysplasia (O2 Dependence at the Later of 28 Days of Age or 36 Weeks Postmenstrual Age)

• 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:
  • Laryngeal Mask Airway: 2.0% (1/51) versus 4.8% (2/42) on control; risk difference -2.8 percentage points (95% CI -10.3 to 4.7), risk ratio 0.41 (0.04–4.38); unadjusted two-proportion z-test p = 0.447.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Laryngeal Mask Airway and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results are broadly consistent with an uncertain comparison rather than a clear pattern of benefit for either approach. The mean number of surfactant doses was 1.6 in each group. For pneumothorax and bronchopulmonary dysplasia, the reported risk-difference intervals include no difference and allow effects in either direction. This overall pattern does not materially sharpen the primary finding.

Secondary outcomes provide context about treatment exposure and other clinical events, but they do not replace the primary endpoint. Similar reported mean surfactant doses do not establish similar efficacy, while the secondary binary outcomes do not resolve whether one delivery approach changes the probability of primary failure. The outcomes measure different aspects of care and should not be combined into an overall conclusion without an analysis plan specifying how they relate.

The registry lists other secondary measures, including days on respiratory support, complications during airway insertion, and mortality. Numerical secondary summaries for these measures are not reported in the registry record. Their absence means that the full range of planned secondary information cannot be assessed from the posted results.

Unadjusted secondary results carry less weight because multiple outcomes create more opportunities for chance findings, especially when no multiplicity procedure or hierarchy is reported. The registry reports no analyses, and it does not state which secondary comparisons were confirmatory or how they were selected. Accordingly, secondary estimates are best treated as descriptive and hypothesis-generating. They can suggest questions for future study, but they do not provide independent confirmation of the primary comparison.

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

• Number of Surfactant Doses
• Days on Any Respiratory Support
• Rate of Pneumothorax
• Rate of Bronchopulmonary Dysplasia (O2 Dependence at the Later of 28 Days of Age or 36 Weeks Postmenstrual Age)
• Number of Participants With Complications During Insertion of LMA or Endotracheal Tube
• Mortality Rate

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference represent?

The primary outcome counts participants who met the failure definition in each group. A risk is the proportion of participants in a group who experienced the event. The risk difference compares those proportions by subtracting the endotracheal-intubation group's risk from the laryngeal-mask group's risk. A negative estimate therefore indicates a lower observed event risk in the laryngeal-mask group; a positive estimate would indicate a higher observed risk in that group.

For the primary outcome, the estimated risk difference is -0.090. This is an unadjusted comparison based on the posted group summaries. It does not account for any covariates or other features of participants. The registry record does not report an adjusted primary analysis.

How should the confidence interval and p-value be read?

A confidence interval expresses statistical uncertainty around an estimated effect. In general, a wider interval indicates less precision, while an interval that includes no difference means the data are compatible with no group difference as well as with effects in either direction. The primary interval runs from -0.264 to 0.085, so it includes zero. This means the result does not rule out no difference and does not rule out a difference favoring either group.

The unadjusted p-value of 0.311 describes how unusual a result at least as far from the null would be under a statistical model in which there is no group difference. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of an effect. Interpreting it alongside the estimate and interval is more informative than treating a threshold alone as decisive.

What do the ratio measures add?

The registry also reports a risk ratio and an odds ratio for the primary comparison, each with an interval. General statistical interpretation: a risk ratio compares event risks as a ratio, while an odds ratio compares event odds. Values at the null correspond to no relative difference. Their intervals include the null, consistent with the uncertainty in the risk-difference result. These measures express the comparison on different scales; they do not provide independent evidence because they are derived from the same group outcomes.

What does intention-to-treat mean?

The primary population is identified as an intention-to-treat analysis. In general, this approach analyzes participants according to their randomized groups, regardless of whether they received the assigned procedure exactly as intended. It preserves the randomized comparison better than an analysis that reallocates participants by treatment received. The registry record does not explain how missing outcome data, withdrawals, or deviations from assigned treatment were handled, so the practical implementation cannot be fully assessed.

Why do binary outcomes need careful interpretation?

For a binary outcome, each participant is classified as having or not having the event under the specified definition. The event counts and group sizes determine the estimated risks. When event counts are limited, estimates can be unstable and confidence intervals can be wide. The primary result should therefore be read as an uncertain estimate rather than a precise measure of the difference likely to occur in another study.

Why can over-dispersion matter in other types of outcomes?

General statistical explanation: over-dispersion occurs when outcome variation is greater than assumed by a chosen statistical model. If it is ignored, standard errors can be too small and intervals or tests can appear more certain than warranted. The primary outcome is reported as a participant count with a binary event definition, not as a count of repeated events per participant. The registry does not report a model-based analysis or an over-dispersion assessment, so no such adjustment should be inferred.

What does the registry report about analyses?

The registry reports no analyses. The comparison estimates and p-values described for the posted outcomes are unadjusted summaries, not evidence of a reported sponsor analysis beyond those results. The record does not report a statistical analysis plan, any planned interim analyses, covariate adjustments, or multiplicity procedures. Those choices should not be assumed from the numerical results alone.

11. Confidence Intervals and Precision

The primary estimate is a risk difference of -0.090, and its 95% confidence interval extends from -0.264 to 0.085. Because this interval includes zero, the posted result is compatible with no difference between the approaches. It is also compatible with a lower event risk in the laryngeal-mask group or a higher event risk in that group. The interval is wide enough to leave clinically consequential differences in either direction unresolved; the registry does not specify a threshold for what would count as clinically important.

The point estimate is only one summary of the data. It should not be read as the exact effect that would recur in another population or setting. The interval describes sampling uncertainty under the statistical calculation, not all sources of uncertainty. It does not account for possible limitations in trial conduct, outcome assessment, missing data, or selective reporting.

The unadjusted p-value is 0.311. This is consistent with the interval's inclusion of no difference, but neither the p-value nor the interval demonstrates equivalence. Establishing equivalence would require a stated margin and an analysis designed to assess whether the full interval lies within that margin. Such a margin is not reported in the registry record.

For the primary result, the reported counts are 12 events among 42 participants in the endotracheal-intubation group and 10 among 51 in the laryngeal-mask group. The relatively limited event information contributes to uncertainty in estimating group risks. The findings therefore support a cautious description of the observed data, not a precise conclusion about the true difference.

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 illustrative calculations based on the observed effect, not the trial's original design assumptions. For these binary outcomes, the figures are participants per arm, not total events. The stated 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 the stated fraction of the observed effect. The trial's own original sample-size assumptions are not reported in the registry record.

For the primary outcome, planning for 100% of the observed effect gives 357 participants per arm for 80% power and 477 participants per arm for 90% power. Planning for 75% of the observed effect gives 654 participants per arm for 80% power and 875 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,515 participants per arm for 80% power and 2,028 participants per arm for 90% power.

In plain language, the 80% power column gives the estimated number per group that would yield an 80% chance of detecting the specified effect under the calculation assumptions if that effect were the true one. The 90% column uses a higher target chance of detection and therefore calls for more participants. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants per arm.

These are planning illustrations, not observed power. They do not show the probability that the trial's observed result is correct, and they do not change the uncertainty in the posted estimate. The primary calculation is especially sensitive to the observed effect used as its starting point; a different plausible effect would produce different planning needs.

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 = 0.286; treatment proportion p₁ = 0.196; average p̄ = 0.241.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6048 = 1.1853.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6014 = 0.5062.
4. n = (1.1853 + 0.5062)² / (-0.0896)² = 356.1, rounded up to 357 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 <- 0.285714285714286                          # control proportion
p1 <- 0.196078431372549                          # 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(2164734)
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 = 357 (80% power), 477 (90% power)
 75% of observed effect: n per arm = 654 (80% power), 875 (90% power)
 50% of observed effect: n per arm = 1,515 (80% power), 2,028 (90% power)
power.prop.test: 356.1 
Simulated power at n = 357 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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study assesses multiple outcomes, comparisons, or analysis choices. Even if each test is considered separately, examining many results can increase the chance that at least one appears noteworthy by chance. This trial has a primary outcome and multiple secondary outcomes, including continuous and binary measures. The registry record does not report a method for controlling multiplicity, a hierarchy for interpreting outcomes, or a distinction between confirmatory and exploratory secondary analyses.

The registry lists no reported analyses. It does not report an analysis plan specifying which comparisons were planned, whether covariates would be adjusted for, how model assumptions would be assessed, or whether any interim analyses were planned. These methods cannot be inferred from the reported estimates. The unadjusted p-values should consequently be interpreted as individual comparisons rather than as results protected against the broader set of possible analyses.

The primary population is described as intention-to-treat, but the record does not report how missing outcome information was handled, whether any participants lacked outcome data, or whether sensitivity analyses were conducted. It also does not report how protocol deviations or crossovers were addressed. Without these details, readers cannot determine whether all randomized participants contributed to the posted primary estimate or how robust the estimate is to missingness.

The record reports randomized allocation and no masking. It does not describe allocation concealment or blinded outcome assessment. These omissions do not establish that the procedures were inadequate, but they limit evaluation of possible bias. The reason for termination is also not reported. In combination, the absent analysis and missing-data details make it important to avoid treating the posted unadjusted results as a complete account of every planned analysis.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cardiopulmonary resuscitation (2.4%).

The registry reports serious adverse events in 1 participant in the endotracheal-intubation group and 0 participants in the laryngeal-mask group. Other adverse events were reported in 3 participants and 1 participant, respectively. Deaths were reported in 1 participant in the endotracheal-intubation group and 0 in the laryngeal-mask group. The registry also lists cardiopulmonary resuscitation as a serious adverse event term at 2.4%.

These figures are descriptive counts, not proof that an event was caused by the assigned airway approach. The registry record does not provide a causal attribution for the event counts, nor enough detail to compare the nature, timing, severity, or relatedness of every event. With few reported events, the absence of a reported event in a group should not be interpreted as evidence that the risk is zero. Safety findings should be considered alongside the limited size and termination status of the trial and the uncertainty in the primary comparison.

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

The primary data describe the number of participants who met a defined failure outcome after rescue surfactant was delivered through one of two airway approaches. The observed counts were 12 in the endotracheal-intubation group and 10 in the laryngeal-mask group. The estimated risk difference favors the laryngeal-mask group, but its confidence interval includes no difference and extends in both directions. The posted result therefore does not establish a clear difference between the approaches.

This is not evidence that the approaches are equivalent. Equivalence is a specific conclusion that requires an appropriate design, a stated margin, and an analysis that excludes differences beyond that margin. The registry record does not report an equivalence or non-inferiority margin. Likewise, a non-significant p-value does not prove that there is no effect.

The outcome combines invasive mechanical ventilation with criteria related to oxygen requirement and surfactant retreatment. Since the record does not report results for each component separately, the primary count cannot show which component contributed to the observed failures. The findings also do not establish effects on longer-term outcomes or on secondary outcomes for which numerical results are not reported.

The trial's results describe this randomized comparison as recorded in the registry. They should not be generalized automatically to other populations, settings, or clinical practices. The open-label design, unreported details about allocation and missing-data handling, lack of a reported analysis plan, and unexplained termination status all limit a fuller assessment. The data offer an estimate with substantial uncertainty, rather than a definitive answer about comparative efficacy or safety.

17. Why This Trial Matters Statistically

This trial is statistically important because it illustrates the difference between an observed direction and a well-established treatment effect. The primary point estimate is lower for the laryngeal-mask group, but the confidence interval includes no difference and permits effects in either direction. A reader should not mistake the direction of the estimate for proof that the intervention improves the outcome.

The study also illustrates why effect estimates and precision matter alongside p-values. The unadjusted p-value of 0.311 does not establish absence of an effect; the interval shows how much uncertainty remains. The registry's planning illustrations show that detecting smaller effects under the stated assumptions would require larger groups, but those illustrations are not a substitute for the trial's actual design rationale or for evidence from observed results.

Finally, this record demonstrates how registry results can be limited by incomplete reporting. The primary population is identified, but information about missing outcomes, allocation procedures, planned analyses, multiplicity, and the reason for termination is not reported. Those omissions affect the interpretation of precision and possible bias. Careful statistical reading keeps the numerical result in view while distinguishing what the record supports from what it leaves unresolved.

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 are specific to this record. The trial is listed as terminated, but the reason is not reported. The enrollment recorded is 93, and the primary result includes group counts of 42 and 51; the record does not explain whether the reported results include every randomized participant or whether any outcome data were missing.

The study is open label. The registry does not report the method used to generate the randomized sequence, whether allocation was concealed, or whether outcome assessment was blinded. Since the primary outcome includes clinical criteria, the absence of information about blinded assessment limits evaluation of possible ascertainment bias.

The endpoint is a composite failure definition. The registry reports the combined primary count but not separate results for invasive ventilation, oxygen requirement, repeat dosing, or total doses. It is therefore not possible to tell from the primary result which criteria drove the observed events.

The analysis record is sparse: no analyses are reported, and the statistical analysis plan, missing-data methods, multiplicity approach, interim analyses, and covariate adjustments are not reported in the registry record. Several listed secondary measures lack numerical results, further restricting assessment of outcomes beyond the primary result and the secondary results with posted summaries. The trial's original sample-size rationale is not reported, so the planning illustrations should not be mistaken for its intended design.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Surfactant Via Endotracheal Tube vs. Laryngeal Mask Airway (LMA) in Preterm Neonates With Respiratory Distress Syndrome — NCT02164734.
• Registry record last updated 2023-09-21; status last verified 2023-08.
• Results first posted 2023-09-21.
• 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

NCT02164734 is a randomized, parallel-group, open-label Phase 4 trial sponsored by Albany Medical College. It compared rescue surfactant delivery through endotracheal intubation after remifentanil and atropine pre-medication with delivery through a laryngeal mask airway after atropine pre-medication in preterm neonates with respiratory distress syndrome. Enrollment is recorded as 93, and the study status is terminated.

The primary outcome counted participants who failed to avoid invasive mechanical ventilation or met specified clinically equivalent criteria within 120 hours. The posted primary estimate favors the laryngeal-mask group, but its confidence interval includes no difference and the unadjusted p-value is 0.311. The registry does not report the reason for termination, the original sample-size assumptions, or a detailed analysis plan. The result is therefore best read as an uncertain estimate, not as proof of superiority, equivalence, or absence of an effect.