Pulmonx Endobronchial Valves Used in Treatment of Emphysema (LIBERATE Study): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pulmonx Endobronchial Valves Used in Treatment of Emphysema (LIBERATE Study) (NCT01796392), a randomized na study. The primary outcome is Forced Expiratory Volume in 1-second (FEV1).

2. Clinical Question

The registry identifies the primary endpoint as a count of participants meeting the threshold, analyzed in the Intent-to-Treat Population. The posted group counts are 61 of 128 in the valve-plus-management group and 10 of 62 in the management group. The estimated proportions are 0.477 and 0.161, respectively. The comparison is expressed as optimal medical management minus valve treatment plus optimal medical management, so its negative risk difference indicates a lower estimated proportion meeting the threshold in the management group.

This is a question about a defined lung-function response at a specified follow-up point. It does not, by itself, describe every participant’s lung function, the size of each participant’s change, or the full balance of benefits and harms. The registry also posts three secondary outcomes at 1 year: absolute change in post-bronchodilator FEV1, St. George’s Respiratory Questionnaire score and 6-minute Walk Distance.

3. Trial Design

LIBERATE is a completed randomized, open-label, parallel-group study sponsored by Pulmonx Corporation. The registry lists an enrollment of 190 and identifies emphysema as the condition under study. The listed study dates are 2013-07 for start and 2017-09 for primary completion. The phase is listed as not applicable.

The two groups differed by the addition of Zephyr Valve endobronchial valve treatment in one group. Both groups were assigned optimal medical management, although their descriptions phrase smoking cessation support somewhat differently: the valve group description includes a smoking cessation program, while the management-only description says support if necessary. Both descriptions include pulmonary rehabilitation, usual medications and oxygen supplementation as necessary.

Randomized allocation means the trial was designed to assign participants to groups by chance; the record does not report the sequence-generation or allocation-concealment procedures. Masking is listed as none. The registry therefore does not describe the study as blinded, and it does not report separate masking arrangements for participants, clinicians or outcome assessors. The parallel model indicates that participants were assigned to one group rather than moving between the two interventions.

The primary endpoint was assessed at 1 year post-procedure and concerns the proportion meeting a greater-than-15% improvement threshold in post-bronchodilator FEV1. The primary population is identified as Intent-to-Treat. The registry lists three secondary outcomes, also with a 1-year timeframe. Although the registry gives enrollment and group counts for the posted results, its original sample-size justification and the assumptions used to design the trial 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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat Population

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 Forced Expiratory Volume in 1-second (FEV1), measured over 1 year.

The primary endpoint is the number and proportion of participants whose post-bronchodilator forced expiratory volume in one second (FEV1) improved by more than 15% at 1 year post-procedure. FEV1 is the volume of air forcibly exhaled during the first second of a forced expiration. The registry specifies that measurement follows bronchodilator therapy and describes the threshold as clinically significant.

Using a threshold turns a continuous measurement into a binary outcome: each participant either meets the specified improvement criterion or does not. The resulting group comparison addresses how often the defined response occurred, rather than the average amount of FEV1 change. That distinction matters because two groups can differ in the proportion crossing a threshold without the binary endpoint describing the full distribution of individual changes.

A threshold can make a result easier to interpret against a prespecified response definition, but it also discards information about changes that fall short of, or exceed, the cutoff. The primary result therefore should be read together with the continuous secondary outcome, FEV1 post-bronchodilator absolute change, which is also posted for 1 year. The registry record does not report the detailed measurement procedures, the rationale for selecting the threshold, or how observations unavailable at the assessment time were handled.

7. Results Posted in the Registry

• Optimal Medical Management: 16.1% (10/62) versus 47.7% (61/128) on control; risk difference -31.5 percentage points (95% CI -44.1 to -18.9), risk ratio 0.34 (0.19–0.61); unadjusted two-proportion z-test p = <0.001.

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.

FEV1 Post-bronchodilator Absolute Change

• 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:
  • Optimal Medical Management: mean -0.00 versus 0.10 on control; difference -0.10 (95% CI -0.16 to -0.04), standardized effect d = -0.52; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Optimal Medical Management than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

St. George's Respiratory Questionnaire (SGRQ)

• 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:
  • Optimal Medical Management: mean -0.50 versus -7.60 on control; difference 7.10 (95% CI 2.38 to 11.82), standardized effect d = 0.45; z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Optimal Medical Management than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

6-minute Walk Distance

• 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:
  • Optimal Medical Management: mean -26.30 versus 13.00 on control; difference -39.30 (95% CI -64.02 to -14.58), standardized effect d = -0.48; z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Optimal Medical Management than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span a continuous lung-function measure, a respiratory questionnaire score and walking distance. Taken together, they broaden the description beyond the primary endpoint’s yes-or-no threshold for FEV1 improvement. Their reported comparisons are in the same general direction of a difference between the assigned groups, and each has an unadjusted p-value below 0.05. This pattern is consistent with the primary result in the limited sense that the outcomes do not all point to an absence of group separation.

These endpoints are not interchangeable. A continuous FEV1 change describes an average change on the lung-function scale, while SGRQ and 6-minute Walk Distance concern different measured outcomes. Their results therefore add distinct information rather than repeat the primary endpoint. A consistent pattern can be informative, but the registry summaries do not establish that one outcome explains another or that all differences have the same clinical meaning.

The secondary findings carry less inferential weight than the primary result because they are additional comparisons, and the registry does not report an adjustment for testing multiple outcomes. When many hypotheses are tested, the chance of at least one apparently notable result can increase. Adjustment methods can address that issue, but none is reported in the registry record. The individual unadjusted p-values should consequently be interpreted as descriptive evidence for each comparison rather than as a family-wise confirmatory conclusion.

The record does not state whether the secondary outcomes were prespecified in a detailed analysis plan, whether there were additional unposted outcomes, or how missing measurements were handled. The posted pattern is therefore useful context for the primary endpoint, but it cannot replace a documented multiplicity strategy, an account of outcome selection or sensitivity analyses. It also should not be treated as proof that every measured aspect of health changed in a consistent way.

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

• FEV1 Post-bronchodilator Absolute Change
• St. George's Respiratory Questionnaire (SGRQ)
• 6-minute Walk Distance

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary comparison estimate?

The primary outcome is binary: a participant either meets the registry’s greater-than-15% FEV1 improvement threshold or does not. The posted group counts and estimated proportions describe the frequency of meeting that criterion in each group. A risk difference is the subtraction of one group’s proportion from the other’s. Here, the reported comparison is oriented as optimal medical management minus valve treatment plus optimal medical management. The negative estimate therefore describes a lower response proportion for the management-only group on this coding.

A risk difference is expressed on the probability scale, so it describes an absolute gap in proportions rather than a relative ratio. The registry also includes relative measures, including a risk ratio and an odds ratio. These use different scales and should not be confused with the risk difference. All such measures depend on the same event definition and group data; they are not separate outcomes or independent evidence.

How should the p-value be understood?

A p-value assesses how compatible the observed data are with a specified null comparison, under the statistical model used. The posted primary p-value is unadjusted and is reported as p < 0.001. It is not the probability that the null hypothesis is true, nor does it quantify the size or clinical importance of the contrast. The effect estimate and its confidence interval provide information about magnitude and uncertainty that a p-value alone cannot convey.

The registry comparison is presented as an unadjusted summary-statistic comparison. The record does not report a detailed sponsor analysis for the primary result, a regression model, covariate adjustment, a stratification scheme or other implementation details. The exact original analysis plan and trial-specific significance threshold are not reported in the registry record.

How are the continuous outcomes different?

The secondary outcomes FEV1 absolute change, SGRQ score and 6-minute Walk Distance are posted as means with standard deviations in each group. A mean describes the group’s average observed change or score as recorded; a standard deviation describes the spread of participant values around that mean. The comparison is a mean difference, with its sign determined by the order of subtraction used in the posted result. The registry comparison uses optimal medical management minus valve treatment plus optimal medical management.

A mean difference retains the continuous scale of an outcome, unlike the primary endpoint’s binary threshold. Its interpretation depends on the outcome’s measurement scale and the way changes are coded. The posted standard deviations describe variability among participants; they are not confidence intervals around the mean. The mean-difference confidence interval instead describes uncertainty in the estimated group contrast under the calculation’s assumptions.

What can and cannot be inferred from the summaries?

Summary-statistic comparisons are useful for describing group-level differences, but they do not reveal individual participant trajectories or the shape of the outcome distributions. The registry lists the primary analysis population as Intent-to-Treat. It does not report the missing-data approach, how participants without an observed 1-year measure entered the calculations, whether any sensitivity analyses were conducted, or the detailed handling of protocol deviations. These details can affect the interpretation of group estimates and cannot be reconstructed from the posted summaries alone.

The registry lists zero reported analyses for the primary outcome and no reported analyses for the secondary outcomes. That means the registry record does not supply a separate detailed analysis report for these results. It does not establish which methods were used outside the material recorded in the registry. A reader should distinguish the posted group summaries and unadjusted comparisons from a fully documented statistical analysis plan.

Why does over-dispersion matter in general?

In general, a binary outcome can be analyzed using models that assume a particular relationship between the mean response and its variability. If observed variation is greater than the model expects, standard errors can be too small and confidence intervals too narrow unless the analysis accounts for that extra variation. This issue is often described as over-dispersion. The posted primary comparison is a simple unadjusted comparison of proportions, and the registry does not report a model-based dispersion assessment. It would therefore be inappropriate to claim that an over-dispersion adjustment was used or required in this analysis.

For continuous outcomes, uncertainty in a mean difference depends on the group sizes and variability as well as on assumptions behind the calculation. The posted standard deviations and group sizes allow the accompanying calculations to describe these comparisons, but the registry does not report diagnostics of distributional assumptions or a detailed model. General statistical principles help explain what the measures mean; they do not fill in unreported trial methods.

Finally, a confidence interval and a p-value address sampling uncertainty under specified assumptions. Neither resolves questions about endpoint selection, missing follow-up, bias from unmasked assessment, multiplicity or generalizability. Those issues require design and analysis information beyond the numerical contrast itself, and several of those details are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.315, with a 95% confidence interval from -0.441 to -0.189. Because the comparison is management-only minus valve-plus-management, the interval’s negative values correspond to a lower estimated response proportion in the management-only group. The interval does not include zero, the value representing equal proportions for this contrast. Its span also shows that the posted estimate is not a perfectly precise single value: a range of differences remains compatible with the calculation and its assumptions.

In general, a confidence interval is a range of estimates generated by a method that accounts for sampling variation. A 95% confidence interval does not mean there is a 95% probability that the fixed true effect lies within this particular calculated interval. Its interpretation depends on the method’s assumptions, including how the observations and analysis are represented. It does not account automatically for missing-data bias, multiplicity, unmasked assessment or other sources of uncertainty.

The secondary mean-difference comparisons also have confidence intervals, while the arm-level summaries include standard deviations. These quantities answer different questions: standard deviations describe the spread of observed participant values, and confidence intervals describe uncertainty in an estimated comparison. The primary interval should not be read as an interval for an individual participant’s response or as a prediction range for a future participant.

Precision is also distinct from clinical importance. A narrow or non-zero interval cannot establish whether a difference matters to participants, and statistical uncertainty does not capture every design limitation. The registry does not report additional analyses of the primary result, such as sensitivity analyses for missing data or adjusted estimates, that could show how robust the interval is to alternative assumptions.

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 sample-size figures are planning illustrations based on the observed effect, not the original trial design. For these outcomes, the entries are participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario targets the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future planning scenario to have an 80% chance of detecting the stated effect, if the assumptions and effect size used in the calculation hold. The 90% power column applies the same idea with a higher target chance of detection. These are design quantities, not guarantees about the outcome of a future study. The entries are per arm, not combined totals. The table’s effect scenarios describe planning for 100%, 75% or 50% of the observed effect.

Smaller effects require more participants to detect under otherwise unchanged assumptions. Thus the scenarios using a smaller fraction of the observed effect have larger participant requirements. The curve represents this planning relationship across effect assumptions; it should be read as a guide to design sensitivity, not as an additional trial result. The required sample size also depends on assumptions such as the significance level, allocation and approximation, so different planning choices can yield different figures.

These calculations are not observed power. Observed power is not a useful substitute for interpreting the confidence interval and effect estimate after a study is complete. The planning figures instead illustrate how the sample size might change if a future study sought to detect a smaller or larger effect under the stated assumptions. They do not establish that the completed study was designed around those assumptions.

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 = 0.477; treatment proportion p₁ = 0.161; average p̄ = 0.319.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6591 = 1.2918.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6203 = 0.5220.
4. n = (1.2918 + 0.5220)² / (-0.3153)² = 33.1, rounded up to 34 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 <- 0.4765625                          # control proportion
p1 <- 0.161290322580645                          # 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(1796392)
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 = 34 (80% power), 44 (90% power)
 75% of observed effect: n per arm = 64 (80% power), 85 (90% power)
 50% of observed effect: n per arm = 151 (80% power), 201 (90% power)
power.prop.test: 33.1 
Simulated power at n = 34 per arm: 0.826 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and three posted secondary outcomes. It does not report a multiplicity adjustment or a hierarchy for interpreting the secondary tests. Without such a plan, the unadjusted secondary p-values should be treated cautiously: testing several outcomes can increase the chance of finding one or more small p-values even when no corresponding underlying differences exist. The registry record does not report whether the study used another approach to control this issue.

Missing-data handling is also not reported in the registry record. The primary population is described as Intent-to-Treat, but that label alone does not specify what happened when a participant had no 1-year outcome measurement, withdrew, or otherwise lacked an observed endpoint. The record does not describe imputation, assumptions about missingness, sensitivity analyses, or whether any participants were excluded from particular outcome calculations. The posted group counts should not be taken as evidence that every assigned participant had complete follow-up.

The registry does not report detailed analysis-population definitions for the secondary outcomes. It also does not report whether the primary comparison was adjusted for baseline values, study site or other covariates, or whether subgroup or interim analyses were conducted. These omissions do not demonstrate that such procedures were absent from all trial documentation; they mean they are not reported in the registry record.

These details matter because analytic choices affect how uncertainty and potential bias are assessed. Randomization supports a comparison of assigned groups, but incomplete follow-up, outcome selection and multiple testing can complicate interpretation. A complete statistical analysis plan and detailed report would be needed to evaluate those choices. The registry results remain interpretable as posted summaries and unadjusted comparisons, but they do not provide that full accounting.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: chronic obstructive pulmonary disease (33.9%), pneumothorax (31.2%), pneumonia (8.1%), arrhythmia (3.2%), diverticulitis (3.2%).

The registry lists serious adverse events for 77 of 128 participants in the Zephyr Valve Treatment and Optimal Medical Management group and 24 of 62 in the Optimal Medical Management group. Other adverse events are listed for 124 of 128 and 46 of 62, respectively. Deaths are listed for 5 participants in the valve-plus-management group and 1 participant in the management-only group.

These are counts of participants recorded in the adverse-event groups, not evidence that an event was caused by the assigned treatment. The registry does not report an adjusted safety comparison or, in these summaries, the timing and relatedness of each event. Serious adverse-event terms listed include chronic obstructive pulmonary disease, pneumothorax, pneumonia, arrhythmia, diverticulitis and respiratory failure, with percentages recorded for those terms. The denominator and group attribution for each listed percentage are not reported in the registry record.

Safety counts should be considered alongside, but separately from, the primary efficacy endpoint. Differences in group size and event definitions matter when interpreting counts. The posted figures alone do not establish comparative risk, causality or the full clinical context of an event.

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

The primary result describes a difference between randomized groups in the proportion meeting a particular FEV1 improvement threshold at 1 year. It is evidence about that endpoint, at that follow-up point, in the population and under the definitions recorded in the registry. The estimated proportions are higher in the valve-plus-management group than in the management-only group, and the posted unadjusted risk-difference interval excludes zero.

That finding does not mean every participant receiving valve treatment met the threshold, nor does it describe the amount of change for each participant. The binary endpoint reduces a continuous measurement to whether the stated cutoff was crossed. The continuous FEV1 outcome and the other secondary measures add different information, but their unadjusted results do not settle all questions about clinical importance or multiplicity.

The randomized design is relevant to the comparison, but the record identifies no masking and does not give detailed methods for allocation, missing data or analysis implementation. The findings should not be extended automatically to populations, settings or follow-up periods that are not described by the registry record. The posted results also cannot establish why a difference arose, or whether each recorded adverse event was related to treatment.

Statistical evidence and clinical interpretation are not the same. A p-value below a conventional threshold indicates how the data compare with a null model under stated assumptions; it does not determine whether an observed difference is important to patients. The registry calls the FEV1 threshold clinically significant, but it does not report the rationale or supporting validation for that cutoff. The full meaning of the result therefore depends on clinical context and supporting evidence beyond the numerical comparison.

Finally, the safety counts and efficacy estimates answer separate questions. Neither should be used alone to make a treatment decision. The registry record reports a randomized comparison and its posted outcomes; it does not provide individual medical advice or a complete assessment of every possible benefit, harm or patient circumstance.

17. Why This Trial Matters Statistically

This trial is statistically instructive because its primary outcome uses a clinically defined threshold applied to a continuous lung-function measure. The resulting comparison is a difference in proportions, not a mean FEV1 difference. Reading the endpoint definition and the contrast direction is essential: the reported risk difference is coded as management-only minus valve-plus-management, so its negative sign has a specific group interpretation.

The study also illustrates why effect estimates, confidence intervals and p-values should be considered together. The primary p-value indicates a strong departure from an equal-proportion comparison under the unadjusted calculation, while the confidence interval conveys a range of plausible contrast sizes under its assumptions. Neither statistic substitutes for an assessment of clinical importance, missing-data sensitivity or the full analysis plan.

Its posted outcomes invite a distinction between a primary test and secondary evidence. Several outcomes have unadjusted comparisons, but the registry does not report multiplicity control. A pattern across outcomes can add context without carrying the same confirmatory status as a prespecified primary endpoint with a documented analysis strategy.

Finally, the record makes visible both useful design features and reporting gaps. Randomization and a parallel-group comparison are stated, while masking is listed as none. The registry identifies the primary analysis population but does not detail missing-data methods or the original sample-size rationale. Separating what the registry reports from what it leaves unspecified is central to sound statistical interpretation.

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 the information recorded for this trial. It is open-label, with masking listed as none. The registry does not report whether outcome assessors were masked or give further detail about the procedures used to generate and conceal allocation. This limits assessment of potential measurement or implementation biases from the record alone.

The primary endpoint is dichotomized at a greater-than-15% FEV1 improvement threshold. That makes the response proportion straightforward to describe but does not retain the full range of individual FEV1 changes. The registry does not report the rationale for the cutoff or details of how post-bronchodilator measurements were obtained. The continuous FEV1 secondary outcome helps describe a different aspect of the data but does not remove the limitations of the primary definition.

The record does not report how missing 1-year data were handled, whether outcome analyses used all assigned participants, or whether sensitivity analyses were conducted. Although the primary population is labeled Intent-to-Treat, the detailed analysis rules are not reported. Multiplicity adjustment for the secondary outcomes is also not reported, so their unadjusted p-values warrant less weight than a result interpreted under a documented testing plan.

Safety summaries lack, in the listed data, a detailed account of event timing, relatedness and group-specific attribution for each serious-event term. The record also does not provide a complete statistical analysis report or original sample-size justification. These are reporting limitations of the registry record; they do not establish what may have been documented elsewhere.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Pulmonx Endobronchial Valves Used in Treatment of Emphysema (LIBERATE Study) — NCT01796392.
• Registry record last updated 2023-06-15; status last verified 2023-05.
• Results first posted 2019-03-05.
• 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

NCT01796392, Pulmonx Endobronchial Valves Used in Treatment of Emphysema (LIBERATE Study), is listed as a completed, randomized, open-label, parallel-group study sponsored by Pulmonx Corporation. The registry records enrollment of 190 and primary completion in 2017-09.

The primary endpoint is the proportion in the Intent-to-Treat Population with more than 15% improvement in post-bronchodilator FEV1 at 1 year post-procedure. The posted comparison favors the valve-plus-management group on that binary endpoint, with an unadjusted risk difference of -0.315 for management-only minus valve-plus-management (95% CI -0.441 to -0.189; p < 0.001).

Three secondary outcomes and adverse-event counts are also posted. The registry record does not report detailed missing-data methods, multiplicity handling or the trial’s original sample-size assumptions.