Efficacy and Safety of Inhaled Molgramostim (rhGM-CSF) in Autoimmune Pulmonary Alveolar Proteinosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Inhaled Molgramostim (rhGM-CSF) in Autoimmune Pulmonary Alveolar Proteinosis (NCT02702180), a randomized phase 2 study. The primary outcome is Absolute Change From Baseline of Alveolar-arterial Oxygen Concentration (A-a(DO2)) After 24 Weeks of Treatment.

2. Clinical Question

The main clinical question is about the average change in a physiological measure, rather than the proportion of participants who crossed a predefined response threshold. The registry reports comparisons of each molgramostim schedule with placebo; it does not describe a direct comparison between the two schedules. That distinction matters: the results address whether each assigned schedule differs from placebo on the measured endpoint, not whether one active schedule is superior to the other. The trial also collected measures of walking distance, respiratory questionnaire score, whole lung lavage, and adverse events. Those secondary outcomes provide additional context, but they do not replace the primary question.

3. Trial Design

This was a randomized, quadruple-masked, parallel-group, placebo-controlled phase 2 study sponsored by Savara Inc. It enrolled 139 participants with autoimmune pulmonary alveolar proteinosis. The registry lists the study as completed, with a start date of 2016-03-21 and primary completion on 2019-04-19.

The 24-week double-blind period included three assigned regimens: once-daily molgramostim, intermittent molgramostim, and once-daily placebo. The intermittent schedule used molgramostim for 7 days followed by placebo for 7 days, repeated for 12 cycles. The registry also describes an open-label intermittent molgramostim regimen for 24 or 48 weeks after completion of the double-blind period. The open-label group is reported separately in safety information and should not be treated as another randomized blinded comparison.

For the primary endpoint, the registry gives analyzed group sizes of 45 for once-daily molgramostim, 43 for intermittent molgramostim, and 43 for placebo. It explicitly notes that not all participants in the full analysis set had blood gas analysis at Week 24. These endpoint-specific counts therefore differ from the total enrollment and should be used when reading the primary outcome estimates.

Random allocation and masking can reduce some sources of systematic difference between groups, while a parallel design assigns participants to a regimen rather than having each participant receive every regimen. The registry does not report the randomization procedure, allocation concealment details, the specific roles included in quadruple masking, or the original sample-size justification. It also does not report the detailed protocol for handling missing primary endpoint measurements.

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: A total of 235 participants were screened, and 138 were randomized and treated. 1 participant in the MOL-INT group and 1 participant in the PBO group withdrew between the double-blind period and the open-label period. 1 participant who withdrew from the double-blind period entered the open-label period.

Double-blind Treatment Period

Reasons for not completing this period:

Open-label Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS): all randomized participants, analyzed according to randomized treatment. Not all participants in the FAS had blood gas analysis done at Week 24, therefore the overall number of participants analyzed is less than the total number of randomized participants.

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 Absolute Change From Baseline of Alveolar-arterial Oxygen Concentration (A-a(DO2)) After 24 Weeks of Treatment, measured over From baseline to 24 weeks.

The primary endpoint was absolute change from baseline in alveolar-arterial oxygen concentration difference, A-a(DO2), from baseline to 24 weeks, measured in mmHg. Blood gas analysis used an arterial blood sample collected while the participant was supine after resting for at least 10 minutes, or longer if needed to reach stable oxygen saturation. The sample was analyzed for arterial oxygen tension (PaO2) and partial pressure of carbon dioxide (PaCO2); the A-a(DO2) calculation was made centrally using a protocol formula.

As general physiological context, the alveolar-arterial oxygen difference compares oxygen pressure in the alveoli with oxygen pressure in arterial blood. It is used as a measure of how effectively oxygen moves from the lungs into the blood. A change from baseline describes how this measure shifted over the treatment period; it is not, by itself, a direct measure of how a participant feels or functions.

The registry reports group means and standard deviations for change, along with comparisons against placebo. The primary analysis population was the full analysis set, with participants analyzed according to randomized treatment. Because some participants did not have Week 24 blood gas analysis, the analyzed endpoint counts are smaller than the total randomized enrollment. The registry does not report a threshold defining a clinically important change, so the size of a mean difference should be interpreted as a difference on the measured scale, not as proof of a particular degree of clinical benefit.

7. Results Posted in the Registry

• Molgramostim Once Daily: mean 28.60 versus 32.00 on control; difference -3.40 (95% CI -12.35 to 5.55), standardized effect d = -0.16; z-test p = 0.457.
• Molgramostim Intermittent: mean 29.30 versus 32.00 on control; difference -2.70 (95% CI -10.94 to 5.54), standardized effect d = -0.14; z-test p = 0.521.

8. Secondary Efficacy Endpoints

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

Change From Baseline in 6-minute Walking Distance (6MWD) After 24 Weeks of Treatment

• 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:
  • Molgramostim Once Daily: mean 39.60 versus 6.00 on control; difference 33.60 (95% CI -7.20 to 74.40), standardized effect d = 0.35; z-test p = 0.107.
  • Molgramostim Intermittent: mean 11.30 versus 6.00 on control; difference 5.30 (95% CI -32.69 to 43.29), standardized effect d = 0.06; z-test p = 0.785.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Molgramostim Once Daily 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 Molgramostim Intermittent and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in St. George's Respiratory Questionnaire (SGRQ) Total Score After 24 Weeks of Treatment

• 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:
  • Molgramostim Once Daily: mean -12.30 versus -4.70 on control; difference -7.60 (95% CI -13.27 to -1.93), standardized effect d = -0.56; z-test p = 0.009.
  • Molgramostim Intermittent: mean -12.00 versus -4.70 on control; difference -7.30 (95% CI -13.19 to -1.41), standardized effect d = -0.52; z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Molgramostim Once Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Molgramostim Intermittent than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the evaluation beyond the primary oxygen-gradient measure. They include six-minute walking distance, St. George's Respiratory Questionnaire total score, whole lung lavage, and adverse-event measures. For the reported adjusted comparisons, the walking-distance estimates have 95% confidence intervals that include zero, while the respiratory questionnaire estimates have intervals that do not include zero. These endpoints therefore do not present a uniform pattern across outcome types. Their scales and meanings differ, so a numeric change in one cannot be treated as directly comparable to a change in another.

The primary endpoint remains the trial's main prespecified question in the registry record. Secondary results can offer supporting or contrasting information, but they do not alter the uncertainty around the primary ANCOVA estimates. The respiratory questionnaire findings are secondary and should not be used alone to conclude that the primary endpoint showed a corresponding effect. Conversely, results on the primary physiological measure do not settle questions about walking distance, quality-of-life scores, or event outcomes.

Multiplicity is a central reason to give unadjusted secondary results less weight. When several outcomes and comparisons are assessed, some apparently notable results can arise by chance, even if each individual test is conducted correctly. The registry lists multiple secondary outcome measures, but does not report whether the secondary tests were adjusted for multiplicity or how their hierarchy was specified. Accordingly, the secondary p-values should be regarded as nominal unless the record documents otherwise.

Numerical results for some listed secondary measures, including lavage and several adverse-event outcomes, are not reported as comparative efficacy estimates in the outcome information. Their listing as planned or collected outcomes is not itself evidence of a group difference. Read together, the secondary findings describe a mixed and incomplete picture rather than a single consistent confirmation of the primary result.

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

• Change From Baseline in 6-minute Walking Distance (6MWD) After 24 Weeks of Treatment
• Change From Baseline in St. George's Respiratory Questionnaire (SGRQ) Total Score After 24 Weeks of Treatment
• Number of Whole Lung Lavage During 24 Weeks of Treatment
• Number of Adverse Events (AEs) During 24 Weeks of Treatment
• Number of Serious Adverse Events (SAEs) During 24 Weeks of Treatment
• Number of Adverse Drug Reactions (ADRs) During 24 Weeks of Treatment
• Number of Severe AEs During 24 Weeks of Treatment
• Number of Participants With at Least 1 AE Leading to Treatment Discontinuation During 24 Weeks of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports the primary endpoint as a continuous measure summarized by its mean and standard deviation. Each participant's outcome was the change from baseline in A-a(DO2) by 24 weeks. A mean describes the center of the observed group changes, while the standard deviation describes how spread out individual changes were around that group mean. These are different quantities: the standard deviation is not the uncertainty interval for the mean or the treatment contrast.

What does the reported ANCOVA estimate represent?

The sponsor-reported comparisons used analysis of covariance (ANCOVA) and are expressed as least-square means (LSmeans). In general, ANCOVA estimates group differences while accounting for covariates included in the model. An adjusted estimate can differ from a direct subtraction of the displayed group means because it is based on the model rather than only on the unadjusted summaries. The registry does not report which covariates were included, how they were selected, or other detailed model specifications. The sponsor's reported estimate and inference therefore describe the registry's stated analysis; the available information is not enough to reconstruct all of its modeling choices.

What is an unadjusted recalculation?

The recalculated comparisons use the posted means, standard deviations, and group sizes to form simple, unadjusted mean differences. For the primary endpoint, the comparison is active-group mean change minus placebo mean change. A negative estimate means the displayed mean change in the active group was numerically lower than the placebo mean change. That sign describes the arithmetic direction; it does not, without clinical context, establish that the difference is beneficial or harmful. The recalculated standard errors and confidence intervals use the group summary statistics and do not account for any covariates that may have entered the ANCOVA.

Because the recalculations are unadjusted, their p-values should not be confused with the sponsor's ANCOVA p-values. They are a transparent summary-statistic-based check, not a replacement for the registry's own model. Here, the discrepancy flag is false, but the estimates still differ because the methods estimate contrasts in different ways. The recalculated results are not evidence that the adjusted analysis is incorrect.

How should confidence intervals and p-values be understood?

In general, a confidence interval expresses uncertainty around an estimated contrast under the assumptions of the analysis. A wider interval means that a broader range of values remains compatible with the data and method. When an interval includes zero for a difference, it includes no average difference as one possibility; this does not prove that the true difference is exactly zero. A p-value summarizes how unusual the observed data, or more extreme data, would be under a specified null model. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of an estimate.

The reported 95% confidence intervals for the primary ANCOVA comparisons each include zero. The recalculated unadjusted intervals also include zero. The numerical estimates remain informative about direction and scale, but their uncertainty limits how narrowly the trial identifies the average contrast. A judgment about clinical importance would also require a clinically meaningful threshold, which is not reported in the registry record.

Why can over-dispersion matter?

General explanation: for continuous outcomes, substantial variability among individual measurements makes a group mean less precise unless the sample size is large enough to offset that variability. The standard deviations reported for the primary endpoint describe variation in observed change. A spread that is large relative to the estimated treatment contrast yields less precise comparisons. The primary results display that uncertainty through their confidence intervals. Over-dispersion is especially discussed for count outcomes, where the variability can exceed what a simple count model expects; the posted primary endpoint is continuous, and the registry does not report a count-model analysis for it.

What does the analysis population tell the reader?

The registry says the primary analysis used the full analysis set, defined as all randomized participants analyzed according to randomized treatment. It also notes that not all participants in that set had Week 24 blood gas analysis. Therefore, the endpoint-specific group sizes reflect those with outcome data used in the posted summaries, not all enrolled participants. The registry does not report the amount or pattern of missingness by reason, whether missing values were imputed, or sensitivity analyses for missing outcomes. Without those details, the possible effect of missing endpoint data cannot be fully assessed.

The registry also lists multiple secondary outcomes, including continuous measures and event counts. The statistical interpretation of a continuous mean difference differs from that of a count or participant-with-event measure. Detailed methods for each secondary analysis, including covariate adjustment and handling of incomplete follow-up, are not reported in the registry record. As a general principle, when many outcomes and comparisons are examined, chance findings become more likely unless the analysis plan accounts for multiplicity. The registry does not report whether such an adjustment was used for secondary results, so nominal secondary p-values warrant more caution than a single prespecified primary comparison.

11. Confidence Intervals and Precision

Precision is about how narrowly the data estimate a group difference. The primary ANCOVA estimate for once-daily molgramostim versus placebo was -4.6 mmHg, with a 95% confidence interval from -11.1 to 2.0. For intermittent molgramostim versus placebo, the estimate was -2.8 mmHg, with a 95% confidence interval from -9.3 to 3.7. Each interval includes zero and spans values on both sides of zero, so neither comparison identifies a single direction with high precision.

The intervals also show why a point estimate should not be read alone. The estimate is the model's central value for the contrast, while the interval conveys uncertainty around it. A confidence interval is not a range containing a fixed percentage of individual participant responses; it concerns the estimated group contrast under the analysis method. The registry does not give a clinical-importance threshold for A-a(DO2), so the intervals cannot be classified as ruling out clinically meaningful effects on the basis of a threshold absent from the record.

Endpoint availability is relevant to precision and interpretation. The primary analysis included 45 participants in the once-daily group, 43 in the intermittent group, and 43 in the placebo group, and the registry notes that not all participants in the full analysis set had Week 24 blood gas analysis. Missing-data reasons and sensitivity analyses are not reported in the registry record. The displayed confidence intervals describe statistical uncertainty under the reported analysis; they do not by themselves capture possible bias if missingness is related to outcome.

The unadjusted recalculated intervals are wider in range than the sponsor-reported ANCOVA intervals for these comparisons, and are based on the posted summary statistics rather than the adjusted model. They provide another view of uncertainty but should not be substituted for the registry's reported analysis. More generally, limited precision means that the data allow a range of plausible contrasts; it does not mean that every value in that range is equally likely or that the endpoints of the interval are treatment effects observed in individual participants.

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 sample sizes. The planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Its target effect is the stated fraction of the observed effect. For example, the primary once-daily comparison lists 625 participants per arm for 80% power and 836 participants per arm for 90% power when planning for 100% of the observed effect. Planning for 75% of that observed effect lists 1,111 participants per arm for 80% power and 1,487 participants per arm for 90% power.

The 80% and 90% columns describe design targets: under the planning assumptions and specified effect, they indicate the number of participants per arm associated with the respective chance of detecting that effect using the stated test framework. The 90% target is more demanding than the 80% target, so it calls for more participants per arm in these illustrations. Smaller target effects also require more participants because they are harder to distinguish from the variability in outcomes. The corresponding values depend on the endpoint and comparison, so entries from different outcomes should not be treated as interchangeable.

These are planning illustrations based on observed effects, not the trial's original design justification. The original sample-size assumptions are not reported in the registry record. This is not observed power: it does not measure whether the completed trial had a particular probability of finding a result after the data were collected. For all non-time-to-event outcomes, the planning values are participants per arm; time-to-event planning figures, if present, would instead be total events. The outcomes reported for this trial are not time-to-event outcomes.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -3.400; pooled standard deviation σ = 21.444.
2. n = 2 × (1.96 + 0.842)² × 21.444² / -3.400² = 624.4, rounded up to 625 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -3.4                      # observed difference in means
sigma <- 21.4436335215059                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2702180)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 625 (80% power), 836 (90% power)
 75% of observed effect: n per arm = 1,111 (80% power), 1,487 (90% power)
 50% of observed effect: n per arm = 2,498 (80% power), 3,344 (90% power)
power.t.test: 625.4 
Simulated power at n = 625 per arm: 0.801 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry's own primary analyses compare each molgramostim schedule with placebo using ANCOVA and report least-square mean differences, 95% confidence intervals, and p-values. For once-daily molgramostim, the sponsor-reported adjusted difference was -4.6 mmHg, with a 95% confidence interval from -11.1 to 2.0 and p = 0.169. For intermittent molgramostim, it was -2.8 mmHg, with a 95% confidence interval from -9.3 to 3.7 and p = 0.397.

The recalculated values are simple unadjusted comparisons based on posted group means and standard deviations. They are not a reconstruction of the ANCOVA, since the registry does not report the covariates or full model specification. The unadjusted estimates and p-values consequently differ from the sponsor's adjusted estimates and p-values. Both approaches give primary confidence intervals that include zero, but they should be identified by their method rather than blended into a single result.

Because the discrepancy flag is false, there is no flagged disagreement requiring a special precedence statement. The sponsor's reported ANCOVA remains the registry's own inferential analysis; the recalculation is supplementary context from summary statistics. Neither should be interpreted as a treatment recommendation. The record does not report enough model detail to reproduce the sponsor's estimate independently.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports one primary endpoint and multiple secondary outcomes. It presents two active-versus-placebo primary comparisons and multiple secondary comparisons. Testing several hypotheses creates a multiplicity issue: without an appropriate plan, the chance of at least one apparently notable finding can increase as more comparisons are considered. The registry does not report whether a multiplicity adjustment was applied, how the primary comparisons were controlled as a family, or whether a hierarchy or gatekeeping strategy was specified. Therefore, secondary p-values should not be treated as adjusted confirmatory evidence.

The primary analysis population is described as the full analysis set, with all randomized participants analyzed according to randomized treatment. However, the record explicitly notes that not all participants in that set had Week 24 blood gas analysis. This means the primary outcome summaries use fewer participants than the total randomized enrollment. The record does not report the reasons for missing blood gas assessments, the amount of missingness by treatment group beyond the endpoint group sizes, or whether missingness was related to participant condition or treatment experience.

Methods for handling missing primary outcomes are not reported in the registry record. In particular, the registry information does not specify whether the analysis used imputation, a missing-at-random assumption, or sensitivity analyses under alternative assumptions. These are not interchangeable choices: missing-data assumptions can affect the estimated contrast and its uncertainty. The stated full analysis set definition clarifies randomized-treatment assignment for analysis, but does not explain how unavailable Week 24 outcomes were handled.

The registry also does not report the covariates used in the primary ANCOVA, details of any interim analysis, or the original sample-size justification. Absence of these details does not demonstrate that a particular procedure was or was not used; it limits what can be independently evaluated from the registry record. This matters when interpreting adjusted estimates, secondary comparisons, and the precision of results.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 4% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: alveolar proteinosis (12.8%), pneumonia bacterial (2.2%), diverticulitis (2.2%), cough (2.2%), dyspnoea (2.2%).

During the double-blind period, the registry reports serious adverse events in 8 of 46 participants at risk in the once-daily molgramostim group, 5 of 45 in the intermittent molgramostim group, and 8 of 47 in the placebo group. These are reported counts and denominators; they should be read as group-specific safety summaries, not as proof that an event was caused by the assigned treatment. The registry also reports zero deaths in each of these double-blind groups.

For the open-label intermittent molgramostim group, serious adverse events were reported in 16 of 130 participants at risk, with zero deaths. This group had open-label follow-up for 24 or 48 weeks from completion of the double-blind period, so it is not directly comparable to the blinded groups as though follow-up conditions were identical. The record lists alveolar proteinosis as a serious adverse event term at 12.8%, along with bacterial pneumonia, diverticulitis, cough, dyspnoea, and laryngeal oedema at 2.2% each. The registry information does not establish a causal relationship from these terms or percentages.

Safety counts need context about the population at risk, follow-up period, event definitions, and exposure. The posted figures alone do not establish equivalence in safety between groups, and absence of a reported death does not mean that no serious events occurred. The record's counts should be interpreted descriptively alongside the trial's design and the limits of the available follow-up details.

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

The result describes average change in a specified blood-gas measure over 24 weeks among participants with available Week 24 endpoint data, analyzed according to randomized treatment. The adjusted estimates compare each molgramostim schedule with placebo. Their confidence intervals include zero, so the registry results do not establish a precise average difference on this endpoint. The estimates also do not prove that the schedules and placebo have exactly the same effect.

These findings are tied to this phase 2 trial, its enrolled aPAP population, the two molgramostim schedules, the placebo regimen, and the reported follow-up. They should not be generalized automatically to other populations, treatment schedules, durations, or outcomes. The registry includes an open-label intermittent regimen after the double-blind period, but that follow-up is not the same randomized blinded comparison as the primary 24-week analysis.

A group mean is not a prediction for an individual participant. It can conceal variation in individual changes, and the standard deviations indicate that individual observations were spread around their group means. The primary endpoint is a physiological measure; it does not directly report symptoms, daily function, or a participant's overall experience. Secondary measures address some other aspects, but their results have their own uncertainty and multiplicity considerations.

Statistical uncertainty is also distinct from clinical importance. The registry does not report a threshold for a clinically important A-a(DO2) change, so the estimates cannot be classified against such a benchmark from this record alone. Likewise, a p-value is not a measure of the probability that treatment works or does not work. The results support a bounded interpretation: they estimate treatment contrasts on the recorded outcomes, with uncertainty, under the analyses and available data described by the registry.

No medical decision follows from these registry statistics alone. The findings do not settle all questions about molgramostim, aPAP, safety, or longer-term outcomes. Missing Week 24 blood gas measurements, unreported analysis details, and the limited scope of a phase 2 comparison are relevant when considering how broadly to interpret the estimates.

18. Why This Trial Matters Statistically

Statistically, this trial is useful because it places two dosing schedules against a placebo comparator while measuring a continuous physiological endpoint under randomized and masked conditions. It reports both group-level changes and adjusted comparisons, allowing readers to distinguish observed group averages from the sponsor's model-based estimates. The separate intermittent and once-daily comparisons also make clear that the schedules are not interchangeable analytic categories.

The results illustrate why estimates and their precision matter more than a single p-value. The adjusted primary contrasts are modest in magnitude relative to their confidence intervals, and those intervals include zero. That combination is more informative than labeling a result simply positive or negative: it shows the estimated direction while also conveying that a range of average differences remains compatible with the analysis.

The registry also allows a useful comparison between reported ANCOVA analyses and simple unadjusted recalculations. These are different methods, with different assumptions and information, and the adjusted model cannot be reconstructed without its covariates. Being explicit about this distinction helps avoid treating an arithmetic contrast from summary data as if it were the sponsor's primary inferential result.

Finally, the record illustrates design and reporting issues that affect interpretation beyond the treatment estimate itself: fewer participants had primary endpoint measurements than were enrolled, several secondary outcomes were assessed, and the record does not detail missing-data handling or multiplicity procedures. Those gaps do not erase the reported findings, but they define what readers can evaluate. The planning illustrations also make clear that a sample-size calculation based on an observed effect is a design aid, not evidence about the completed trial's observed power.

19. Limitations

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

Several trial-specific limitations affect interpretation. The primary endpoint was unavailable at Week 24 for some participants in the full analysis set, and the registry states that the analyzed count was therefore below total enrollment. Reasons for missing assessments, their distribution by group beyond the reported endpoint counts, and sensitivity analyses are not reported in the registry record. The extent to which missing endpoint data could influence the estimated contrasts cannot therefore be determined from the record.

The registry provides ANCOVA estimates but not the covariates or full model specification. It is not possible to reproduce the sponsor's adjusted analysis from the reported group means and standard deviations alone. The unadjusted recalculations offer a separate summary-statistic comparison, but they do not resolve uncertainty about the model specification or missing data.

Multiple secondary outcomes were listed, while details of multiplicity control are not reported. Secondary findings consequently warrant caution, particularly when they differ in scale and interpretation from the primary endpoint. The registry also does not report the original sample-size justification, the randomization implementation, allocation concealment details, or whether interim analyses were conducted.

The trial was phase 2 and assessed the main endpoint through 24 weeks. The record also describes open-label intermittent treatment after the double-blind period, but the open-label follow-up does not provide the same blinded randomized comparison as the primary analysis. The registry information does not establish how broadly findings apply beyond the studied population, schedules, and duration. It also does not report a clinical-importance threshold for the primary endpoint, limiting interpretation of whether the estimated differences are meaningful in practice.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Inhaled Molgramostim (rhGM-CSF) in Autoimmune Pulmonary Alveolar Proteinosis — NCT02702180.
• Registry record last updated 2023-04-12; status last verified 2023-04.
• Results first posted 2022-04-15.
• 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

NCT02702180 was a completed randomized, quadruple-masked, parallel-group, placebo-controlled phase 2 trial sponsored by Savara Inc. It enrolled 139 participants with autoimmune pulmonary alveolar proteinosis. The blinded treatment period compared once-daily inhaled molgramostim, intermittent inhaled molgramostim, and placebo over 24 weeks.

The primary outcome was change from baseline in A-a(DO2), measured by blood gas analysis. The registry's adjusted comparisons against placebo had 95% confidence intervals that included zero. Not all randomized participants had Week 24 blood gas results, and details of missing-data handling, model covariates, and multiplicity control are not reported in the registry record.

Secondary outcomes included walking distance, respiratory questionnaire score, lavage, and safety measures. Open-label intermittent molgramostim follow-up was reported separately from the blinded comparison. The results should be read as estimates with uncertainty for the measured outcomes and follow-up, rather than as a definitive account of every possible benefit or risk.