Improving Patient Outcomes by Selective Implantation of the Zephyr EBV - Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Improving Patient Outcomes by Selective Implantation of the Zephyr EBV - Study (NCT02025205), a randomized na study. The primary outcome is Percentage Change in Forced Expiratory Volume in 1 s (FEV1) (ITT Population).

2. Clinical Question

3. Trial Design

This was a prospective, multicentre, randomized, controlled study of endobronchial valve therapy versus standard of care in homogeneous emphysema. The registry classifies allocation as randomized, masking as none, and the model as parallel. The official title describes a one-way crossover investigation. The record explains that patients assigned to standard of care would cross over to valve treatment after the 6-month visit and continue follow-up for 6 additional months. The primary comparison was planned at 3 months, before that crossover.

The study status is completed. The recorded start was 2014-08, and primary completion was 2016-04. Enrollment is reported as 93. The primary outcome is identified as percentage change in FEV1 in the ITT population, measured at baseline and after 3 months. Follow-up was described as lasting 12 months after randomization. In addition to lung function, the stated objectives included quality of life, exercise capacity, dyspnea, BODE index, target lobe volume reduction, and safety outcomes.

The registry lists an endobronchial valve device intervention. The valve arm is described as endoscopic lung volume reduction with Zephyr valves; standard care is described as optimal drug therapy and medical management according to clinical practice. No masking was reported. Details of the randomization sequence, concealment of allocation, site-specific enrollment, or procedures for implementing the assigned treatments are not reported in the registry record.

The available primary comparison uses group means and standard deviations. The record does not report a detailed statistical analysis plan, the original sample-size justification, or whether interim analyses were planned. Although the registry describes the study as randomized and gives an ITT label for the primary outcome, the precise operational definition of that population and the handling of participants without a 3-month measurement are not reported in the registry record. Those omissions limit assessment of how the analysis was implemented, even though the main comparison and its summary statistics are posted.

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: ITT 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 Percentage Change in Forced Expiratory Volume in 1 s (FEV1) (ITT Population), measured over At baseline and after 3 months.

The primary endpoint is percentage change in forced expiratory volume in 1 second (FEV1) from baseline to the 3-month visit. FEV1 is the volume of air a person can exhale in the first second of a forced breathing maneuver. The registry identifies the result as a mean percentage change and specifies the ITT population. The comparison is between patients assigned to valve therapy and patients assigned to standard of care.

FEV1 is used as a measure of airflow limitation and lung function. In a trial of a lung-volume-reduction procedure, measuring change from baseline gives a way to compare the direction and size of lung-function changes over follow-up between randomized groups. The endpoint is not a direct measure of symptoms, daily functioning, quality of life, or survival; those are separate clinical domains. Nor does a group mean show the range of individual responses.

The registry reports the endpoint at baseline and after 3 months. This early time point makes the assigned-group comparison distinct from the later crossover described for the standard-of-care group. The posted result is a group-level summary, not a measure of how many individual patients improved by a particular amount. The registry record does not report a threshold defining a clinically important change in FEV1, so the statistical estimate alone cannot determine how participants would value the magnitude of change.

7. Results Posted in the Registry

• BLVR With Zephyr Endobronchial Valves: mean 13.70 versus -3.20 on control; difference 16.90 (95% CI 7.73 to 26.07), standardized effect d = 0.79; 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.

Absolute Change in FEV1 (L) Post Bronchodilator at 3 Months

• 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:
  • BLVR With Zephyr Endobronchial Valves: mean 0.10 versus -0.02 on control; difference 0.12 (95% CI 0.05 to 0.19), standardized effect d = 0.78; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for BLVR With Zephyr Endobronchial Valves than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Absolute Change in FEV1 (% Predicted) Post Bronchodilator at 3 Months

• 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:
  • BLVR With Zephyr Endobronchial Valves: mean 3.40 versus -1.30 on control; difference 4.70 (95% CI 2.44 to 6.96), standardized effect d = 0.87; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for BLVR With Zephyr Endobronchial Valves than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Absolute Change in Residual Volume (RV) at 3 Months

• 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:
  • BLVR With Zephyr Endobronchial Valves: mean -0.40 versus 0.10 on control; difference -0.50 (95% CI -0.87 to -0.13), standardized effect d = -0.56; z-test p = 0.008.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for BLVR With Zephyr Endobronchial Valves than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcome summaries broadly align in direction with the primary lung-function result: the posted FEV1 measures favor the valve group on their reported change scales, while the residual-volume comparison is negative for the valve group relative to standard care. That pattern is consistent with changes across related physiological measures, but the endpoints are not interchangeable. Each represents a different measurement, and agreement in direction does not establish that every planned clinical domain changed in the same way.

The registry’s secondary objectives also include target lobe volume reduction, quality of life, exercise capacity, dyspnea, BODE index, and safety. The available outcome descriptions name several of these measures, but numerical findings for the broader symptom, functioning, and quality-of-life domains are not reported in the registry record. The fact that an outcome was listed as an objective does not itself show whether it improved or how large any change was.

Secondary results generally carry less confirmatory weight when the testing strategy is not reported. If many outcomes are examined, some may appear statistically notable by chance even when no underlying difference exists. A multiplicity adjustment or a prespecified hierarchy can address this issue, but neither is described in the registry record. The secondary comparison p-values are unadjusted, so they should be interpreted as exploratory evidence rather than as a set of independent confirmations of the primary finding.

Secondary outcomes can still help assess coherence and broaden understanding beyond a single lung-function measure. Their interpretation depends on the endpoint definition, timing, missingness, and analysis method, as well as whether the observed difference is clinically meaningful. Those details are not fully reported for the secondary analyses. The most defensible overall reading is that the posted physiological summaries point in directions that are broadly compatible with the primary result, while the registry does not provide enough information to make equally strong claims across all stated outcome domains.

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

• Absolute Change in Target Lobe Volume for EBV Group (ITT Population)
• Percent Change in Target Lobe Volume for EBV Group (ITT Population)
• Percent of Subjects in the EBV Group With a Target Lobe Volume Reduction (TLVR) of ≥ 350ml at 3 Months
• Absolute Change in FEV1 (L) Post Bronchodilator at 3 Months
• Absolute Change in FEV1 (% Predicted) Post Bronchodilator at 3 Months
• Absolute Change in Residual Volume (RV) at 3 Months
• Percent Change in Residual Volume (RV) at 3 Months
• Percent Predicted Change in Residual Volume at 3 Months

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary result compares a continuous outcome between randomized groups. The endpoint is percentage change in FEV1, summarized by a mean and standard deviation for each group. A mean describes the arithmetic average of the observed values, while a standard deviation describes how spread out those values are around the mean. These are complementary summaries: the mean gives the central group result, and the standard deviation indicates that individual measurements vary around it.

What does the mean difference represent?

The comparison is the valve-group mean minus the standard-of-care mean. The posted estimate is 16.9. A positive estimate indicates that the valve-group average was higher on the reported percentage-change scale. The estimate is a between-group contrast, not the change experienced by every participant and not a comparison of each participant with themselves across randomized assignments. The two groups’ reported averages are 13.7 and -3.2, respectively.

What does the confidence interval add?

A confidence interval expresses uncertainty in an estimated contrast using a specified statistical procedure. The reported 95% interval is 7.733 to 26.07. In general, if the same study procedure were repeated many times under the same assumptions, intervals constructed in this way would cover the underlying parameter at the stated rate. For this particular result, the interval describes plausible values for the mean contrast under the calculation; it is not a probability statement about a single fixed effect after the data have been observed. It also does not describe where most individual participant outcomes fall.

How should the p-value be read?

The reported unadjusted p-value is < 0.001. In general, a p-value measures how surprising data at least as incompatible with a null model would be if that model and the calculation’s assumptions were correct. It is not the probability that the null is true, a measure of effect size, or a measure of clinical importance. Here, it accompanies an estimate and confidence interval that point in the same direction. The record does not report whether this p-value was adjusted for testing multiple outcomes.

Why do variability and over-dispersion matter?

General statistical explanation: when participants’ outcomes vary considerably, group means are less precise than they would be with less variability at the same group size. The standard deviations reported for the primary outcome are 28.2 in the valve group and 13.0 in standard care. This difference in spread is relevant to understanding why the mean alone is incomplete. Over-dispersion is especially important for count outcomes when observed variation exceeds what a simple count model assumes; the primary endpoint is continuous, and the registry does not describe a count model or an over-dispersion adjustment. No such adjustment should be presumed.

What analysis details are available?

The registry identifies the primary outcome as an ITT result and gives group sizes, means, standard deviations, a mean difference, a confidence interval, and an unadjusted p-value. The record does not report the analysis model, adjustment covariates, treatment of missing measurements, or a detailed definition of the analysis population. The comparison is therefore best read as the posted group-level summary rather than as evidence of a particular adjusted modeling strategy. The discrepancy flag is false, so there is no noted conflict requiring a sponsor analysis to take precedence over a recalculation.

General statistical explanation: random allocation aims to make assigned groups comparable, on average, with respect to measured and unmeasured characteristics. It does not guarantee that every characteristic is balanced in a particular trial. The registry record does not provide a baseline balance assessment in the registry record for this analysis. The reader should therefore distinguish the design’s intended protection against confounding from a full evaluation of trial execution.

The primary comparison is at 3 months, whereas the study description includes crossover after the 6-month visit for the standard-of-care arm. This timing means that the posted primary comparison concerns the randomized groups before the described crossover. Later comparisons could be affected by treatment switching, but later primary analyses are not reported in the registry record. The registry reports no posted analysis records beyond the summary statistics captured for the outcomes.

11. Confidence Intervals and Precision

The primary mean difference is 16.9, with a 95% confidence interval from 7.733 to 26.07. This interval is entirely above zero and therefore supports a positive between-group difference under the calculation used for the posted summary. Its lower and upper limits are meaningfully separated, so the point estimate should not be treated as exact. The interval is the principal description of precision for this contrast; the p-value alone does not convey its range.

Precision depends on both the amount of information and the variability in the outcome. The primary outcome standard deviations are 28.2 for the valve group and 13.0 for standard care, indicating that participants’ values were spread around their respective means. The registry reports group sizes of 43 and 50 for this outcome. These registry entries help contextualize the interval, but they do not reveal whether outcome data were missing or whether all randomized participants contributed to the calculation.

The interval concerns the difference between group means, not the range of treatment effects across individual participants. It does not imply that every participant’s change would fall between 7.733 and 26.07, nor does it quantify variation in personal response. The record does not report a clinically important threshold for this endpoint, so statistical precision cannot by itself establish whether values across the interval represent differences that patients would regard as important.

The comparison is an unadjusted summary-statistic calculation, and the registry record does not report a separate adjusted confidence interval or detailed model. Interpretation should remain tied to the stated groups, outcome, and 3-month time point. The interval does not account for uncertainty from unreported analysis choices or possible missing data unless those features are incorporated in the calculation, which is not described in the registry record.

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’s documented design calculation. The stated illustration assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. For continuous outcomes, the figures are participants per arm, not a combined total. The time-to-event convention would be total events, but the outcomes are continuous.

The 80% power column gives the estimated participants per arm under which a study would have an 80% chance of detecting the specified effect if the assumptions held and the effect were real. The 90% power column uses a higher chance of detection, which generally requires more participants for the same effect and assumptions. These are planning concepts, not guarantees: actual power depends on the true effect, variability, data completeness, and whether the assumptions match the future study.

The rows represent planning for 100%, 75%, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so detecting it generally requires more participants. For the primary outcome, the illustrated values rise from 26 participants per arm for 80% power when planning for 100% of the observed effect to 101 participants per arm when planning for 50% of that effect. The corresponding 90% power illustrations rise from 34 to 135 participants per arm across those same rows.

These figures are not observed power. They do not describe the probability that the completed study’s result is correct or the probability of reproducing it. The original trial’s sample-size assumptions and justification are not reported in the registry record, so the illustrations should be read only as conditional planning examples using the observed effect and the stated 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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 16.900; pooled standard deviation σ = 21.402.
2. n = 2 × (1.96 + 0.842)² × 21.402² / 16.900² = 25.2, rounded up to 26 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 <- 16.9                      # observed difference in means
sigma <- 21.4017253078775                     # 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(2025205)
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 = 26 (80% power), 34 (90% power)
 75% of observed effect: n per arm = 45 (80% power), 60 (90% power)
 50% of observed effect: n per arm = 101 (80% power), 135 (90% power)
power.t.test: 26.2 
Simulated power at n = 26 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

The study lists a primary outcome and a range of secondary outcomes. The registry record does not report a multiplicity strategy, such as adjustment for multiple comparisons, a testing hierarchy, or a distinction between confirmatory and exploratory secondary analyses. When several endpoints are tested, the chance of at least one apparently unusual result can increase. General statistical explanation: multiplicity procedures manage this risk by changing how evidence is assessed across a family of tests. Without a reported plan, unadjusted secondary p-values should not be treated as if they were protected against multiple testing.

The primary comparison has an unadjusted p-value of < 0.001. The secondary summaries also list unadjusted p-values, but an adjustment across the outcome family is not reported in the registry record. The primary result and secondary results therefore do not necessarily have the same evidentiary status. The primary endpoint was designated as primary, while the registry record does not explain whether any secondary outcome was formally prioritized.

The primary population is labeled ITT. In general, intention-to-treat analysis compares participants according to their randomized assignment, regardless of treatment received, helping preserve the benefit of randomization. The registry does not report the operational definition used, whether all randomized participants were included in the posted endpoint calculation, or how deviations from assigned treatment were handled. The missing-data method, amount of missingness, and reasons for missing measurements are also not reported in the registry record.

Missing outcome data can affect interpretation if participants with unavailable measurements differ systematically from those with observed measurements. General statistical explanation: complete-case analyses, imputation, and model-based approaches make different assumptions about missingness, and those assumptions can influence estimates. No particular approach can be attributed to this trial from the available registry entries. The record also does not report sensitivity analyses assessing the effect of missing data.

These omissions do not erase the posted results, but they limit independent assessment of their robustness. A detailed statistical analysis plan, population definition, missing-data accounting, and multiplicity approach would help clarify which analyses were prespecified and how uncertainty across outcomes was controlled. Those details are not reported in the registry record.

15. 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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: copd exacerbation (30.2%), pneumothorax (25.6%), dyspnea (7.0%), hypercapnia (6.0%), diagnostic bronchoscopy (4.7%).

The registry lists serious adverse events for the valve and standard-of-care groups. In the valve group, 28 participants were affected among 43 at risk; in standard care, 16 were affected among 50 at risk. These are counts of participants affected as recorded in the outcome fields, not a comparison adjusted for differences in exposure time or other factors. The record also reports other adverse events affecting 30 participants among 43 at risk in the valve group and 22 among 50 at risk in standard care.

Serious event terms listed include COPD Exacerbation at 30.2%, Pneumothorax at 25.6%, Dyspnea at 7.0%, Hypercapnia at 6.0%, Diagnostic bronchoscopy at 4.7%, and Pneumonia at 4.0%. The registry entries do not specify the arm for each percentage in this list, so these percentages should not be assigned to a particular group. The death counts are not reported in the registry record.

Adverse-event summaries describe events observed and recorded during the study; they do not by themselves establish that treatment caused an event. Group sizes and follow-up exposure differ, and the record does not provide enough detail to interpret event timing, recurrence, severity beyond the serious classification, or attribution. These figures should be read as safety reporting, not as a standalone causal comparison.

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

The posted primary result indicates a higher mean percentage change in FEV1 at 3 months for the group assigned to Zephyr valve treatment than for the group assigned to standard of care. The estimated difference is 16.9, and its 95% confidence interval, 7.733 to 26.07, is above zero. This is evidence of a group-level statistical difference in the reported endpoint under the summary-statistic comparison. It is not a guarantee of benefit for every participant or a complete account of the treatment’s effects.

Statistical evidence and clinical meaning are related but distinct. The registry record does not report a threshold for a clinically important FEV1 change, and the endpoint is not itself a direct measurement of quality of life, symptoms, exercise capacity, or longer-term outcomes. The study lists those domains among its objectives, but numerical findings for many of them are not reported in the registry record. The primary result therefore cannot stand in for all aspects of patients’ health or experience.

The comparison is limited to the randomized groups and the reported 3-month period. The study description includes a later crossover from standard care to valve treatment after the 6-month visit, so later follow-up would have a different treatment contrast. Detailed later between-group results are not reported in the registry record. The findings also concern patients with COPD and homogeneous emphysema as described in the record; eligibility details needed to judge applicability to other populations are not provided.

Important interpretive information is missing, including the original statistical plan, missing-data handling, multiplicity strategy, and details of the ITT definition. Masking was none. Such features affect confidence in the robustness and scope of the reported estimate. The posted result can be described precisely as a positive mean difference with the stated interval and p-value, while broader claims about individual response, long-term effects, or comparative safety are not established by that result alone.

This interpretation is statistical rather than a treatment recommendation. It distinguishes what the registry reports from questions the posted data do not resolve. The outcome, time point, group comparison, and uncertainty should remain attached to any statement about the finding.

17. Why This Trial Matters Statistically

This trial illustrates why the design and timing of a comparison matter when a study includes crossover. The primary endpoint was assessed at 3 months, before the registry’s described crossover of the standard-of-care group after the 6-month visit. That preserves a clear early randomized contrast for the primary result, whereas later comparisons would need to account for the change in treatment assignment described by the protocol.

It also illustrates the value of reporting an effect estimate with a confidence interval rather than relying on a p-value alone. The mean difference of 16.9 and its 95% confidence interval from 7.733 to 26.07 communicate both direction and uncertainty. The group means and standard deviations add context about the average changes and variation among participants. A reader can distinguish the estimated group contrast from individual outcomes and from judgments about clinical importance.

The trial’s multiple outcome domains highlight a common interpretive challenge. Lung-function measures can provide related physiological evidence, while symptoms, activity, quality of life, and safety capture different dimensions. A consistent pattern can support coherence, but unadjusted secondary findings are more vulnerable to chance when many outcomes are considered. The registry record’s lack of a reported multiplicity plan makes that distinction especially relevant.

Finally, the trial shows how registry detail affects statistical appraisal. Randomization, allocation, outcome summaries, and adverse-event counts are reported, but the original sample-size justification, missing-data strategy, detailed model, and analysis plan are not. Planning illustrations based on the observed effect can help readers understand how sample size depends on the effect targeted, yet they cannot substitute for the trial’s original design rationale. Transparent reporting of those methods would make the posted estimates easier to evaluate and reproduce.

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 trial-specific limitations shape interpretation. Masking was none, so participants and study personnel were not masked according to the registry classification. The record does not describe any safeguards for outcome assessment or treatment delivery that might mitigate awareness of assignment. The primary endpoint is a lung-function measure, but the registry entries do not specify who performed measurements or whether assessors were independent.

The study used a one-way crossover design as described in its official title and summary, while the registry classifies the model as parallel. The primary comparison at 3 months comes before the described crossover, but the changing treatment exposure later in follow-up complicates interpretation of later outcomes. Later comparative analyses are not reported in the registry record. The crossover timing and follow-up description should therefore be kept distinct from the primary result.

The record does not report the full eligibility criteria, baseline characteristics, randomization procedures, allocation concealment, or detailed site information. These omissions limit assessment of balance between groups and generalizability. It also does not report the original sample-size assumptions, analysis model, missing-data methods, or sensitivity analyses. Although the primary endpoint is labeled ITT, the precise analysis population and handling of unavailable outcomes are not described.

Adverse-event counts are presented, but the registry entries do not provide complete attribution, timing, exposure-adjusted rates, or death counts. Serious event percentages are listed without a specified arm in the summarized details. The registry record also lacks a reported multiplicity strategy, which limits confirmatory interpretation of secondary tests. These are reporting limitations; they do not by themselves show that the underlying trial procedures were inadequate, but they restrict what can be concluded from the posted registry information.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Improving Patient Outcomes by Selective Implantation of the Zephyr EBV - Study — NCT02025205.
• Registry record last updated 2019-08-16; status last verified 2019-07.
• Results first posted 2019-08-16.
• 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

NCT02025205 is a completed, prospective, multicentre, randomized, controlled study of Zephyr endobronchial valve therapy versus standard of care in COPD with homogeneous emphysema. The registry reports enrollment of 93, no masking, and a parallel model, while the official title and study description include a one-way crossover after the 6-month visit. The primary endpoint was percentage change in FEV1 at 3 months in the ITT population.

The valve group mean was 13.7 and the standard-of-care group mean was -3.2. The reported mean difference was 16.9, with a 95% confidence interval from 7.733 to 26.07 and p < 0.001. The result indicates a positive group-level difference on the reported endpoint, with uncertainty described by the interval. Secondary physiological summaries are broadly compatible in direction, but unadjusted testing, unreported multiplicity and missing-data methods, and limited detail on analysis procedures constrain interpretation. Serious adverse events were reported in both groups; attribution and death counts are not reported in the registry record.