SURFAXIN® Treatment for Prevention of Bronchopulmonary Dysplasia (BPD) in Very Low Birth Weight (VLBW) Infants.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for SURFAXIN® Treatment for Prevention of Bronchopulmonary Dysplasia (BPD) in Very Low Birth Weight (VLBW) Infants. (NCT00215540), a randomized phase 2 study. The primary outcome is Incidence of Death or Bronchopulmonary Dysplasia (BPD) at 36 Weeks.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, placebo-controlled phase 2 trial with quadruple masking. It enrolled 136 participants and compared two lucinactant doses with placebo. The registry record lists Windtree Therapeutics as the sponsor and gives the trial status as terminated. The reason for termination is not reported in the registry record.

The treatment arms were SURFAXIN high dose at 175 mg/kg, SURFAXIN low dose at 90 mg/kg, and placebo. The placebo was described as sham air using a 3.0 mL/kg volume of air. The primary analysis population is described as all randomized infants, analyzed on an intent-to-treat basis. The reported endpoint counts include 45 infants in the high-dose arm, 47 in the low-dose arm, and 44 in the placebo arm.

The trial focused on very low birth weight infants at risk of BPD. The registry summary describes infants who had continued intubation and had received surfactants for prevention or treatment of respiratory distress syndrome. The primary outcome was the number of participants who died or developed BPD at 36 weeks post-menstrual age. Secondary outcomes included BPD at 28 days, BPD at 36 weeks, duration of mechanical ventilation and supplemental oxygen, measures based on inspired oxygen and mean arterial pressure, death or BPD at 28 days, and days in hospital.

The registry record does not report the trial's detailed allocation procedure, masking roles, original statistical analysis plan, or the reason it was terminated. It also does not report the original design assumptions beyond the endpoint text stating that a sample size of 70 per arm was considered sufficient to demonstrate a 20% relative risk reduction.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: A sample size of 70 per arm is sufficient to demonstrate a 20% relative risk reduction. All randomized infants were analyzed (intent-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.

6. Primary Endpoint

The registry lists the primary outcome as Incidence of Death or Bronchopulmonary Dysplasia (BPD) at 36 Weeks, measured over 36 weeks post-menstrual age (PMA).

The primary endpoint was the number of participants who died or developed bronchopulmonary dysplasia by 36 weeks post-menstrual age. BPD was defined in the record as an oxygen requirement at 36 weeks post-menstrual age. This is a binary composite outcome: each infant is counted according to whether death or the specified BPD criterion occurred by the assessment time. The registry describes the outcome as participants with either event, not as a measure of BPD severity.

Combining death and BPD gives the endpoint a way to count two clinically important outcomes within one measure. A composite can increase the number of observed events relative to either component alone, but its interpretation depends on the components and the definition used. In this trial, the published endpoint does not separate the number of deaths from the number of BPD cases among survivors. Component-specific primary results are not reported in the registry record.

For the primary endpoint, the posted arm counts were 26 of 45 in the high-dose group, 37 of 47 in the low-dose group, and 29 of 44 in the placebo group. These counts describe the participants meeting the composite definition; they do not by themselves establish whether the arms differ beyond the uncertainty in the comparison. The endpoint was assessed at 36 weeks post-menstrual age, so it concerns status at that specified time rather than later respiratory outcomes.

7. Results Posted in the Registry

• SURFAXIN High Dose: 57.8% (26/45) versus 65.9% (29/44) on control; risk difference -8.1 percentage points (95% CI -28.2 to 12.0), risk ratio 0.88 (0.63–1.22); unadjusted two-proportion z-test p = 0.430.
• SURFAXIN Low Dose: 78.7% (37/47) versus 65.9% (29/44) on control; risk difference 12.8 percentage points (95% CI -5.4 to 31.1), risk ratio 1.19 (0.92–1.55); unadjusted two-proportion z-test p = 0.171.

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.

BPD at 28 Days

• 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:
  • SURFAXIN High Dose: 93.3% (42/45) versus 86.4% (38/44) on control; risk difference 7.0 percentage points (95% CI -5.5 to 19.5), risk ratio 1.08 (0.94–1.24); unadjusted two-proportion z-test p = 0.276.
  • SURFAXIN Low Dose: 93.6% (44/47) versus 86.4% (38/44) on control; risk difference 7.3 percentage points (95% CI -5.1 to 19.6), risk ratio 1.08 (0.94–1.25); unadjusted two-proportion z-test p = 0.247.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SURFAXIN High Dose 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 SURFAXIN Low Dose and the control. The interval gives the range of effects that remain compatible with the data.

BPD at 36 Weeks

• 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:
  • SURFAXIN High Dose: 57.8% (26/45) versus 65.9% (29/44) on control; risk difference -8.1 percentage points (95% CI -28.2 to 12.0), risk ratio 0.88 (0.63–1.22); unadjusted two-proportion z-test p = 0.430.
  • SURFAXIN Low Dose: 78.7% (37/47) versus 65.9% (29/44) on control; risk difference 12.8 percentage points (95% CI -5.4 to 31.1), risk ratio 1.19 (0.92–1.55); unadjusted two-proportion z-test p = 0.171.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SURFAXIN High Dose 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 SURFAXIN Low Dose and the control. The interval gives the range of effects that remain compatible with the data.

Days Receiving Mechanical Ventilation (MV)

• 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:
  • SURFAXIN High Dose: mean 30.10 versus 35.80 on control; difference -5.70 (95% CI -15.36 to 3.96), standardized effect d = -0.25; z-test p = 0.248.
  • SURFAXIN Low Dose: mean 42.10 versus 35.80 on control; difference 6.30 (95% CI -3.90 to 16.50), standardized effect d = 0.25; z-test p = 0.226.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SURFAXIN High Dose 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 SURFAXIN Low Dose and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover different aspects of respiratory and hospital course, including BPD at an earlier time, mechanical ventilation, supplemental oxygen, oxygen and pressure measures, death or BPD at 28 days, and days in hospital. These outcomes do not all measure the same construct or use the same time window, so a single direction across every measure would not be expected automatically. The posted comparisons show variation in direction between dose groups and outcomes rather than a uniform pattern that independently reinforces the primary result.

The secondary results should be read alongside, not as replacements for, the primary composite endpoint. The primary comparison concerns death or BPD at 36 weeks post-menstrual age. A secondary measure such as BPD at 28 days asks a different question, and a duration measure such as days receiving mechanical ventilation is not directly interchangeable with an event count. A result for one secondary outcome cannot establish the primary endpoint or resolve its uncertainty.

Eight secondary outcomes are listed as posted. The record includes detailed numerical results for some secondary measures, but results for the other listed measures are not reported in the registry record. Across reported analyses, the registry includes categorical methods and ANOVA for the continuous ventilation-duration outcome. The number of analyses in the record is 27, so the collection of results should not be read as though every outcome were a single pre-specified primary test.

When many outcomes or comparisons are examined, the chance of at least one apparently unusual result can increase. Unadjusted secondary p-values do not account for that multiplicity unless a correction is specified. A multiplicity adjustment is not reported in the registry record. This does not make secondary findings meaningless, but it means they are generally less conclusive than a clearly designated primary analysis and require cautious interpretation, especially when the primary comparison itself is imprecise.

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

• BPD at 28 Days
• BPD at 36 Weeks
• Days Receiving Mechanical Ventilation (MV)
• Duration of Supplemental Oxygen
• Area Under the Curve for Fraction of Inspired Oxygen (FiO₂)
• Area Under the Curve for Mean Arterial Pressure (MAP)
• Incidence of Death or BPD at 28 Days
• Days in Hospital

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because each participant either met the death-or-BPD definition at 36 weeks post-menstrual age or did not. The posted counts can be compared as risks, and a risk difference expresses the absolute difference between the treatment-arm risk and the placebo risk. A negative risk difference means the treatment-arm estimate is lower than the placebo estimate; a positive value means it is higher. These directions describe the estimates, not proof that treatment caused the difference.

What does a confidence interval describe?

A confidence interval represents the uncertainty around an estimate under the assumptions of the statistical method used. The primary risk-difference intervals are unadjusted recalculations from the posted counts. When an interval includes zero, the data do not rule out no difference at the confidence level used. An interval extending both below and above zero can also include effects in opposite directions. It is therefore important to read the estimate together with its interval rather than relying on the point estimate alone.

Why are there two kinds of p-values?

The registry reports primary analyses using the Cochran-Mantel-Haenszel method, with p-values of 0.476 and 0.208 for the two dose comparisons. This method is commonly used to combine categorical comparisons across strata. The exact stratification factors used in this trial are not reported in the registry record. The recalculated p-values, 0.43 and 0.171, are unadjusted calculations from the posted summary counts. They do not reproduce the registry's analysis method and should be interpreted as separate, simpler comparisons.

A p-value describes how compatible the observed data are with a specified null hypothesis under the statistical model. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. A p-value also does not remove uncertainty about the estimate. That is why the risk differences and their confidence intervals remain important parts of the interpretation.

How do the secondary analyses differ?

The registry reports ANOVA for the comparisons of days receiving mechanical ventilation. ANOVA is a method for comparing means across groups. The posted means and standard deviations describe the observed distribution in each arm, while a mean difference describes the contrast with placebo. The registry reports p-values of 0.285 for high dose and 0.229 for low dose for this outcome. The registry's reported ANOVA does not include an effect estimate or confidence interval in the results recorded. The unadjusted mean-difference calculations have their own intervals and p-values, which are not the same analysis as the registry's ANOVA.

For binary secondary outcomes, the same general ideas apply as for the primary endpoint: counts describe events, and a risk difference compares the event risks between arms. The choice of outcome definition and follow-up time affects what a comparison means. BPD at 28 days is not the same endpoint as death or BPD at 36 weeks, and duration outcomes are not binary event counts.

What does the sample-size illustration estimate?

The planning illustration uses the observed effect as a starting point and considers smaller fractions of that effect. It gives the number of participants per arm for 80% or 90% power under the listed assumptions. Power is the chance that a planned study would detect an effect of the specified size at the chosen significance level, if that effect and the assumptions were correct. These calculations are planning aids rather than evidence about what the completed trial could or could not detect.

In general, binary outcomes depend on the event frequency as well as the effect being targeted, while continuous outcomes depend on the variability and mean difference. Estimates from a small study can be unstable, so planning directly from an observed effect may lead to very different sample-size illustrations if that estimate changes. The registry record does not report the full original analysis plan, any interim analyses, the factors used for stratification, or the procedures for handling missing observations. Those elements should not be inferred from the methods that can be reconstructed from posted summary results.

11. Confidence Intervals and Precision

The primary risk-difference estimate for high dose versus placebo was -0.081, with a 95% confidence interval from -0.282 to 0.120. For low dose versus placebo, the estimate was 0.128, with a 95% confidence interval from -0.054 to 0.311. Both intervals cross zero, so neither unadjusted interval excludes no difference. Their range also includes estimates in both directions, limiting how precisely the data identify the direction of an effect.

Confidence intervals are not a list of values that are all equally likely, and they do not guarantee that the true effect lies within a particular observed interval. They show the uncertainty associated with an estimate under the method's assumptions. In this trial, the breadth of the primary intervals is important: the estimated differences do not pin down a narrow range of possible effects.

Sample sizes were 45 in the high-dose arm, 47 in the low-dose arm, and 44 in placebo for the primary outcome. With event counts of 26, 37, and 29, respectively, the comparisons have limited precision. The interval for high dose includes values below and above zero; the interval for low dose also includes values on either side. Thus, the observed direction of either point estimate is not enough to establish a reliable direction of difference.

The registry's own primary analyses report p-values but do not report confidence intervals or effect estimates for those analyses. The intervals are unadjusted recalculations from the posted counts, not registry-reported intervals. For secondary outcomes, precision varies by measure, and confidence intervals are not reported for every registry analysis. The record does not provide a basis for assuming that all endpoints were analyzed with the same model or adjustment.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm for 80% power and participants per arm for 90% power. They are not total events. The planning 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 illustration is based on the observed effect, not the original design of the trial.

The 80% power column gives a planning estimate of how many participants would be needed in each arm for an 80% chance of detecting the specified effect under those assumptions. The 90% column uses a higher target probability of detection, so its participant requirement is larger for a given effect. These are planning quantities, not a claim about the probability that the completed trial found a true effect.

Rows for 100% of the observed effect use the full observed estimate as the target. Rows for 75% and 50% use progressively smaller target effects. A smaller effect is harder to distinguish from random variation, so the calculation requires more participants per arm. The values can therefore rise substantially as the target effect becomes smaller. They are illustrative: actual requirements depend on whether the underlying effect, event frequency, variability, and analysis assumptions are close to those used in the calculation.

These figures are not observed power. Observed power is not a useful substitute for reading the estimate and its uncertainty after a study has been completed. The registry record's statement that 70 per arm was sufficient to demonstrate a 20% relative risk reduction is part of the endpoint description, but the full original sample-size assumptions and justification are not reported in the registry record. The planning illustration should not be mistaken for the trial's original design calculation.

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 = 0.659; treatment proportion p₁ = 0.578; average p̄ = 0.618.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6870 = 1.3465.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6846 = 0.5762.
4. n = (1.3465 + 0.5762)² / (-0.0813)² = 559.1, rounded up to 560 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 <- 0.659090909090909                          # control proportion
p1 <- 0.577777777777778                          # 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(215540)
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 = 560 (80% power), 748 (90% power)
 75% of observed effect: n per arm = 985 (80% power), 1,318 (90% power)
 50% of observed effect: n per arm = 2,191 (80% power), 2,932 (90% power)
power.prop.test: 559.1 
Simulated power at n = 560 per arm: 0.801 (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-reported primary comparisons used the Cochran-Mantel-Haenszel method and gave p-values of 0.476 for high dose versus placebo and 0.208 for low dose versus placebo. The recalculated unadjusted comparisons use the posted counts and yield p-values of 0.43 and 0.171. The registry record does not report an effect estimate or confidence interval for its primary analyses, so the unadjusted risk differences and intervals are additional descriptions rather than substitutes for the sponsor's analysis.

The values differ because the methods differ: the reported method is Cochran-Mantel-Haenszel, whereas the recalculation is an unadjusted comparison of summary counts. The record does not identify the strata used in the reported method, so the source of any particular numerical difference cannot be specified further. The registry record does not flag a discrepancy between the posted results and the recalculated results. The sponsor-reported method remains the analysis to cite as the registry's own result, while the recalculation helps show the approximate absolute contrast and its uncertainty from the aggregate counts.

For the secondary continuous outcome of days receiving mechanical ventilation, the sponsor-reported analysis used ANOVA. Its p-values are distinct from the p-values attached to the unadjusted mean-difference recalculations. Across outcomes, readers should keep each analysis tied to its stated method and avoid treating a recalculated unadjusted result as if it were the sponsor's model-based result.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and lists secondary outcomes, with 27 analyses recorded. Multiple outcomes and comparisons create a multiplicity issue: when many hypotheses are tested, some results may appear noteworthy by chance even if there is no corresponding underlying effect. Methods such as a pre-specified testing hierarchy or an adjustment to the significance threshold can address this concern, but a multiplicity procedure is not reported in the registry record. It is therefore not possible to determine from the record how the family of comparisons was handled.

The primary endpoint population is described as all randomized infants analyzed on an intent-to-treat basis. This indicates that assignment, rather than treatment received, defines the primary analysis groups according to the registry description. The record does not give further details about whether every randomized participant contributed an observed primary outcome, how missing primary outcomes were handled, or whether any sensitivity analyses addressed missingness. Those procedures are not reported in the registry record.

Missing data can affect both the estimated event frequency and the uncertainty of a comparison. The impact depends on how much information is missing and on whether missingness is related to outcome or treatment group. Since the registry does not report those details, no assumption about the amount, balance, or handling of missing data should be made. The posted arm counts are useful descriptions, but do not in themselves document a missing-data strategy.

The detailed statistical analysis plan, interim analyses, stratification factors for the Cochran-Mantel-Haenszel comparisons, and adjustment for secondary testing are not reported in the registry record. The trial's termination reason is also not reported. These omissions limit evaluation of whether analyses were fully pre-specified and whether all planned results are represented. They do not establish that a particular method was or was not used; they mark what cannot be determined from the registry record.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: bronchopulmonary dysplasia (20.5%), retrolental fibro-dysplasia (19.1%), intraventricular haemorrhage neonatal (19.1%), patent ductus arteriosus repair (18.2%), sepsis neonatal (13.6%).

The serious adverse event summaries report 33 affected participants among 45 at risk in the high-dose group, 36 among 47 in the low-dose group, and 35 among 44 in the placebo group. The other adverse event summary reports 45 affected among 45 at risk in the high-dose group, 47 among 47 in the low-dose group, and 44 among 44 in the placebo group. These are counts as recorded; the registry record does not provide a full explanation of the definitions or ascertainment procedures for these summaries.

Serious adverse event terms listed include bronchopulmonary dysplasia at 20.5%, retrolental fibro-dysplasia at 19.1%, intraventricular haemorrhage neonatal at 19.1%, patent ductus arteriosus repair at 18.2%, sepsis neonatal at 13.6%, and pneumothorax NOS at 11.1%. These figures describe listed event terms and should not be interpreted as comparative treatment effects. The record does not report death counts in the safety summary, so deaths by treatment arm are not reported in the registry record.

Counts alone do not establish whether an event was caused by an intervention. The safety figures also do not provide a complete account of event timing, duration, severity grading, or treatment attribution in the information recorded.

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

The posted results describe a randomized comparison of two lucinactant doses with placebo in very low birth weight infants at risk of BPD. For the primary composite endpoint at 36 weeks post-menstrual age, the event counts were 26 of 45 for high dose, 37 of 47 for low dose, and 29 of 44 for placebo. The unadjusted risk-difference estimates point in opposite directions for the two dose comparisons, and both confidence intervals include zero. The registry's own reported p-values are 0.476 and 0.208.

These data do not provide a precise estimate of the direction or size of a difference for either dose relative to placebo. An interval that includes zero does not prove that the groups are identical, just as a point estimate on one side of zero does not prove that a difference exists. The trial results should be described as uncertain rather than as establishing either benefit or lack of benefit.

The primary outcome combines death and BPD, and the registry does not report separate primary component results. Its definition of BPD relies on oxygen requirement at 36 weeks post-menstrual age. The results therefore address that recorded composite at that assessment time; they do not by themselves describe later respiratory status, BPD severity, or each component's separate frequency.

The study's phase 2 status, sample sizes, termination status, and unreported details about missing-data handling and multiplicity are relevant context. The record does not state why the trial was terminated. The posted results cannot establish what would have been observed under a different design or in populations not described by the trial. They also cannot establish a causal explanation for differences in observed counts beyond the randomized comparison and the methods recorded.

Overall, the registry reports an informative comparison with substantial uncertainty. The estimates and intervals should be read together, and secondary findings should be treated as supporting context rather than as a replacement for the primary result. No treatment recommendation follows from these registry statistics alone.

18. Why This Trial Matters Statistically

This trial is statistically instructive because it combines a binary composite primary endpoint with two active dose groups and a placebo comparison. Each component of that design shapes interpretation. The composite outcome combines death and BPD, while the two treatment contrasts raise questions about how to interpret direction and uncertainty across doses. The results do not show one common direction for both dose estimates.

The primary interval estimates make clear why a point estimate or p-value alone is insufficient. The unadjusted intervals cover zero and extend into values on both sides, so the estimates are not precise enough to settle the direction of a difference. The reported Cochran-Mantel-Haenszel p-values and the recalculated unadjusted comparisons also demonstrate why methods need to be identified before results are compared: different approaches to the same aggregate counts need not return identical values.

The record also illustrates the distinction between a completed-trial result and a planning calculation. The sample-size illustrations use observed effects and stated assumptions; they are not an account of the original trial's complete design rationale and are not observed power. Separately, the endpoint text records a sample-size statement of 70 per arm and a 20% relative risk reduction, but the broader original assumptions are not reported.

Finally, a registry record can offer useful arm counts and reported analyses while leaving important statistical details unavailable. Here, multiplicity procedures, missing-data handling, interim analyses, and the reason for termination are not reported. Recognizing such limits is part of sound statistical reading: it prevents unsupported certainty while preserving what the posted results can tell readers about the observed data.

19. Limitations

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

The primary comparisons involve 45, 47, and 44 participants in the respective arms. The confidence intervals are broad and cross zero, so the estimates are imprecise. The primary composite also does not separate death from BPD in the posted outcome counts, limiting interpretation of which component contributed to the result.

The registry lists the trial as terminated but does not report the reason. It does not report detailed missing-data procedures, interim analyses, the full original statistical analysis plan, or the factors used in the Cochran-Mantel-Haenszel analyses. Multiplicity adjustment is not reported despite the listed secondary outcomes and analyses. These are gaps in the recorded information; they do not establish that a procedure was absent from the conduct of the trial.

Some secondary outcomes are listed without detailed numerical results in the registry record. The posted secondary results also cover measures with different definitions and follow-up times, which are not interchangeable with the primary composite. Sponsor-reported results for primary comparisons are p-values without accompanying effect estimates or confidence intervals, while the effect estimates described in the recalculation are unadjusted.

The registry describes a specific population of very low birth weight infants who had continued intubation and received surfactants. The extent to which results apply outside that described population is not established by the record. The safety summary also lacks death counts and detailed information about event timing and attribution. These limitations constrain interpretation of both efficacy-related outcomes and adverse event summaries.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: SURFAXIN® Treatment for Prevention of Bronchopulmonary Dysplasia (BPD) in Very Low Birth Weight (VLBW) Infants. — NCT00215540.
• Registry record last updated 2012-06-13; status last verified 2012-05.
• Results first posted 2012-06-13.
• 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

NCT00215540 is a randomized, quadruple-masked, parallel-group, placebo-controlled phase 2 trial of SURFAXIN (lucinactant) for prevention of bronchopulmonary dysplasia in very low birth weight infants. The trial enrolled 136 participants and is listed as terminated. The arms were lucinactant 175 mg/kg, lucinactant 90 mg/kg, and placebo described as sham air.

The primary endpoint was death or BPD at 36 weeks post-menstrual age, with BPD defined as oxygen requirement at that time. The posted primary counts were 26 of 45, 37 of 47, and 29 of 44 for high dose, low dose, and placebo, respectively. The registry reports Cochran-Mantel-Haenszel p-values of 0.476 and 0.208 for the dose comparisons with placebo. Recalculated unadjusted risk-difference intervals include zero for both comparisons.

The record lists secondary outcomes and safety summaries, but does not report several details needed to assess multiplicity, missing-data handling, or the reason for termination. The posted primary results are best read as estimates with substantial uncertainty.