Clinical Study to Evaluate the Efficacy of VR506 Using a New Inhaler for the Treatment of Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Study to Evaluate the Efficacy of VR506 Using a New Inhaler for the Treatment of Asthma (NCT01472757), a randomized phase 2, phase 3 study. The primary outcome is Mean Change From Start of Treatment Baseline to End of Study (Week 12) for In-clinic Morning Pre-Dose Forced Expiratory Volume In 1 Second (FEV1).

2. Clinical Question

3. Trial Design

This completed study evaluated VR506 inhaled from a new device for asthma. The registry identifies the study as phase 2 and phase 3, randomized, quadruple-masked, and parallel-group. Its official title describes a randomized, double-blind, placebo-controlled study in adolescent and adult subjects. The listed interventions were VR506 and placebo, with placebo serving as the control for three VR506 dose groups.

The registry reports enrollment of 374. The primary endpoint is a continuous measure: mean change in in-clinic morning pre-dose FEV1 from baseline to week 12. The listed unit is liters, and the arm-level summaries report means and standard deviations. Endpoint counts differ by comparison and are given for participants with both baseline and end-of-treatment values under the stated LOCF approach; they should not be confused with enrollment.

The study started in 2011-10, had primary completion in 2013-05, and is marked completed. The brief study description says its purpose was to evaluate the clinical efficacy of three VR506 doses delivered through a new dry powder inhaler. The registry record does not report the original sample-size justification or the detailed randomization procedure. It also does not report the masking roles associated with its quadruple-masking designation.

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: 374 subjects were randomised, and 373 received at least one dose of study drug; 1 subject was randomised but not treated.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set analyzed, but number of patients represents subjects with both start of treatment baseline value and end of treatment value where a Last Observation Carried Forward (LOCF) approach was used to impute values of missing post-baseline visits; 2 subjects had no post-dose FEV1 assessments, baseline values were not carried forward

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 Mean Change From Start of Treatment Baseline to End of Study (Week 12) for In-clinic Morning Pre-Dose Forced Expiratory Volume In 1 Second (FEV1), measured over Baseline and 12 weeks.

The primary endpoint measures change in forced expiratory volume in 1 second (FEV1), the volume of air exhaled in the first second of a forced breath, from start-of-treatment baseline to the end of the study at week 12. Measurements were taken in clinic in the morning before dosing, and results are expressed in liters. A change score describes how the measurement shifted over the stated period, while a comparison with placebo helps distinguish the observed change in a dose group from the change in the control group.

FEV1 is a continuous measure, so the registry reports group means and standard deviations. A mean offers a concise summary of the group’s average change; the standard deviation describes how spread out individual changes were around that average. Neither statistic alone shows the full distribution of individual outcomes.

The endpoint is useful for comparing lung-function measurements across randomized groups at a prespecified follow-up point. The record names the endpoint and timeframe, but does not report a clinically meaningful threshold for interpreting a difference in liters. The result therefore describes a measured group difference; it does not by itself establish how important that difference would be to patients.

7. Results Posted in the Registry

• VR506 50 mcg: mean 0.32 versus 0.19 on control; difference 0.13 (95% CI 0.01 to 0.25), standardized effect d = 0.31; z-test p = 0.033.
• VR506 100 mcg: mean 0.38 versus 0.19 on control; difference 0.19 (95% CI 0.09 to 0.29), standardized effect d = 0.57; z-test p = <0.001.
• VR506 250 mcg: mean 0.38 versus 0.19 on control; difference 0.19 (95% CI 0.09 to 0.29), standardized effect d = 0.55; 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.

Mean Change From Start of Treatment Baseline to End of Study (Week 12) for In-clinic Weekly Morning Pre-dose Peak Expiratory Flow (PEF)

• 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:
  • VR506 50 mcg: mean 25.00 versus 1.18 on control; difference 23.82 (95% CI 8.43 to 39.21), standardized effect d = 0.45; z-test p = 0.002.
  • VR506 100 mcg: mean 27.11 versus 1.18 on control; difference 25.93 (95% CI 10.75 to 41.11), standardized effect d = 0.50; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for VR506 50 mcg 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 higher for VR506 100 mcg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes concerning withdrawals due to worsening asthma, weekly morning pre-dose peak expiratory flow (PEF), and acceptability of the device. Numeric results are posted for the continuous PEF outcome, with comparisons reported for the 50 mcg and 100 mcg groups versus placebo. The registry record does not provide posted results for every listed secondary outcome in the same way; absence of a displayed numerical result should not be interpreted as evidence of no difference.

Across the posted PEF summaries, each of the three VR506 group means is higher than the placebo mean. Sponsor-reported ANCOVA p-values are recorded for the 50 mcg and 100 mcg comparisons. These secondary results broadly follow the direction of the primary endpoint’s posted group means, but PEF and FEV1 are different measures and should not be treated as interchangeable confirmation of one another. Secondary outcomes can add context about related lung-function measures and other study questions, but they do not replace the primary endpoint.

The unadjusted recalculations for secondary outcomes are exploratory when considered alongside multiple endpoints and dose comparisons. Testing many questions increases the chance that some findings appear notable by chance unless the analysis plan addresses multiplicity. The registry record does not report a multiplicity adjustment or enough detail to determine how the secondary analyses were prioritized. Accordingly, the secondary findings carry less inferential weight than the trial’s designated primary analysis, and their interpretation should remain cautious.

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

• Number of Participants With Withdrawals Due to Worsening of Asthma
• Mean Change From Start of Treatment Baseline to End of Study (Week 12) for In-clinic Weekly Morning Pre-dose Peak Expiratory Flow (PEF)
• Assessment of Acceptability of the Device

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, and the registry reports a mean and standard deviation for each group. The mean summarizes the average change in FEV1. The standard deviation describes variation among the observed changes: a larger value indicates more spread around the group mean. It is not the uncertainty in the mean itself. That uncertainty also depends on the number of participants contributing endpoint values.

What does a mean difference represent?

The unadjusted recalculation compares each VR506 group’s mean change with the placebo group’s mean change. A positive estimate means the VR506 group’s posted mean change was higher than placebo’s. The recalculation uses the posted group summaries and is not the same as the sponsor-reported ANCOVA. It does not incorporate covariate adjustment unless the posted summaries themselves encode such an adjustment, which the registry does not indicate.

How should a confidence interval be read?

A confidence interval gives a range of values compatible with the data and the method used to calculate it. A narrower interval indicates greater precision than a wider interval, all else being equal. The intervals for the primary mean differences are recalculated, unadjusted intervals, not intervals reported for the sponsor’s ANCOVA. A confidence interval is not a guarantee that the true effect lies within its limits, nor does it indicate whether a difference is clinically important. No clinical-importance threshold is reported in the registry record.

What does the p-value address?

A p-value measures how compatible the observed data are with a specified null hypothesis, under the assumptions of the analysis. It does not measure the size or importance of an effect, and it is not the probability that the null hypothesis is true. The posted primary p-values come from sponsor-reported ANCOVA superiority analyses. The registry gives the method and p-values, but does not provide the ANCOVA effect estimates, confidence intervals, covariates, or further model details. The simple recalculations also report unadjusted p-values; those are not a substitute for the sponsor’s analysis.

Why distinguish ANCOVA from the recalculation?

ANCOVA is a model-based approach that can compare groups while accounting for one or more covariates. In clinical trials, baseline outcome values are often among the candidate covariates, but the registry record does not specify which covariates were included. The recalculation compares summary means without the adjustment details of the sponsor’s model. If the analyses produce different inferential results, the sponsor’s own analysis takes precedence for reporting what the trial concluded statistically. The registry’s limited detail prevents a full audit of that model.

Why do missing values matter?

The primary outcome description refers to a full analysis set, but says the number of patients represents subjects with both baseline and end-of-treatment values. It also states that LOCF was used to impute missing post-baseline visits and notes that 2 subjects had no post-dose FEV1 assessment. LOCF carries the last observed value forward to fill a missing later measurement. This makes an analysis possible for some missing follow-up values, but it relies on an assumption that the carried-forward measurement is an adequate stand-in for the unobserved value. The registry record does not report sensitivity analyses testing alternative missing-data assumptions, or clarify all details of how participants with no post-dose assessment were handled.

Why can variation and group size affect precision?

For a continuous outcome, uncertainty in a group mean depends on both the spread of measurements and the number of observations. Greater variation tends to make an estimate less precise, while more observations tend to improve precision, subject to the analysis assumptions. Differences in endpoint counts and standard deviations across the groups therefore contribute to differences in the recalculated intervals. These general statistical principles do not establish that the model assumptions were met; diagnostics and details of the sponsor’s model are not reported in the registry record.

11. Confidence Intervals and Precision

The recalculated primary mean differences have confidence intervals that quantify their statistical precision under the simple unadjusted method. For VR506 50 mcg versus placebo, the estimate is 0.13 liters, with a confidence interval from 0.011 to 0.249 liters. For VR506 100 mcg versus placebo, the estimate is 0.19 liters, with an interval from 0.094 to 0.286 liters. For VR506 250 mcg versus placebo, the estimate is 0.19 liters, with an interval from 0.089 to 0.291 liters.

The intervals differ in width, indicating different precision across the comparisons. The 50 mcg interval extends closer to zero at its lower end, while the intervals for 100 mcg and 250 mcg have higher lower limits. These are recalculated, unadjusted intervals derived from posted summary statistics. The registry’s sponsor-reported ANCOVA results do not include confidence intervals, so the recalculated intervals should not be described as the precision of the sponsor’s adjusted estimates.

Confidence intervals address statistical uncertainty, not clinical importance. The registry record does not report a threshold for a meaningful FEV1 difference, and the interval limits cannot supply that judgment on their own. Interpretation also depends on the analysis population, missing-data approach, and whether the model assumptions are reasonable; not all relevant details are reported.

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 illustrations express required sample size as participants per arm for 80% power or participants per arm for 90% power. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is expressed as a stated fraction of the observed effect. The trial’s original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative participants per arm for a design with an 80% chance of detecting the specified effect under the listed assumptions, if that effect and the model assumptions were correct. The 90% power column gives the corresponding planning count for a 90% chance. These are design calculations, not probabilities that the observed trial result is correct. Smaller effects require more participants per arm to detect than larger effects, which is why the planning counts rise when planning for 75% or 50% of the observed effect rather than 100%.

For the primary comparisons, the required counts differ by dose because the observed mean differences and pooled variability differ. For example, planning for 100% of the observed effect gives participants-per-arm figures of 160 and 213 for 50 mcg, 48 and 64 for 100 mcg, and 52 and 70 for 250 mcg, at 80% and 90% power, respectively. Planning for a smaller fraction produces larger counts. These illustrations are not observed power, and they do not reconstruct the study’s own design choices.

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 = 0.130; pooled standard deviation σ = 0.414.
2. n = 2 × (1.96 + 0.842)² × 0.414² / 0.130² = 159.1, rounded up to 160 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 <- 0.13                      # observed difference in means
sigma <- 0.413859345685282                     # 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(1472757)
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 = 160 (80% power), 213 (90% power)
 75% of observed effect: n per arm = 283 (80% power), 379 (90% power)
 50% of observed effect: n per arm = 637 (80% power), 852 (90% power)
power.t.test: 160.1 
Simulated power at n = 160 per arm: 0.803 (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 reports sponsor analyses using ANCOVA for each VR506 dose versus placebo. Each comparison is designated as a superiority analysis. The p-values are 0.013 for 50 mcg, <0.001 for 100 mcg, and <0.001 for 250 mcg. No adjusted effect estimates or confidence intervals are included in the registry record.

The recalculated estimates are simple, unadjusted comparisons based on the posted means and standard deviations. They give mean differences of 0.13 liters, 0.19 liters, and 0.19 liters for the respective doses versus placebo, along with unadjusted confidence intervals and p-values. Because the recalculations do not reproduce the sponsor’s ANCOVA, differences between the two analyses may reflect their different methods and inputs.

The registry marks a discrepancy between the sponsor-reported analyses and the recalculations. The sponsor’s own analysis takes precedence when describing the trial’s inferential result. The recalculation remains useful as an independent, transparent comparison of the posted summary statistics, but it should not replace or be presented as a correction to the sponsor’s model. The ANCOVA specification and its adjusted estimates are not reported in the registry record, limiting further comparison.

15. Multiplicity, Missing Data and Analysis Populations

The study includes three VR506 dose-versus-placebo comparisons for the primary endpoint, as well as secondary outcomes. When several hypotheses are tested, the chance of at least one apparently notable result can increase. Statistical methods can account for this multiplicity, but the registry record does not report whether a correction or a prespecified testing hierarchy was used. It also does not report the full statistical analysis plan, so it is not possible to determine how the primary and secondary comparisons were ordered or how the reported p-values should be interpreted across the family of tests.

The primary analyses are reported as ANCOVA superiority comparisons, but the record gives no adjusted estimates, confidence intervals, covariates, or detailed model specification. It does not report interim analyses or stopping rules. These details should not be inferred from the phase designation, the trial status, or the reported p-values.

Missing data are relevant to the primary endpoint. The outcome description says the full analysis set was analyzed, but that the number of patients represents subjects with both start-of-treatment baseline and end-of-treatment values. It says LOCF was used to impute missing post-baseline visits and reports that 2 subjects had no post-dose FEV1 assessment. The record does not provide a complete account of how those subjects were handled, the extent or pattern of missingness by group, or sensitivity analyses using different assumptions. LOCF can preserve observations in an analysis, but it does not remove uncertainty about unobserved outcomes.

The registry record does not report a detailed sample-size justification or the original planning assumptions. The posted power illustrations are based on observed effects and do not document the study’s design rationale. Together, the missing analysis-plan details, limited description of covariate adjustment, and incomplete reporting of missing-data sensitivity analyses constrain independent assessment of the sponsor’s inferential conclusions.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: viral infection (1.1%), appendicitis (1.1%).

The registry reports serious adverse events by group, with the number at risk and the number affected. There were 0 serious adverse events among 91 participants at risk in the placebo group, 1 among 93 at risk in the VR506 50 mcg group, 1 among 95 at risk in the 100 mcg group, and 0 among 94 at risk in the 250 mcg group. The listed serious-event terms are VIRAL INFECTION and APPENDICITIS, each shown as 1.1%. The record does not assign those terms to a particular group in the listed terms.

Deaths are reported as 0 in each group. The registry also reports other, non-serious adverse events: 47 affected among 91 at risk for placebo, 42 among 93 for 50 mcg, 40 among 95 for 100 mcg, and 33 among 94 for 250 mcg. These counts are descriptive. They do not establish that an event was caused by treatment, and comparisons should account for the fact that safety denominators differ from the primary endpoint counts. The registry’s adverse-event summary alone is not a complete assessment of comparative safety.

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

The posted results describe average changes in morning pre-dose FEV1 over the study period and comparisons of those changes between randomized groups. The placebo mean was 0.19 liters; the VR506 group means were 0.32 liters for 50 mcg and 0.38 liters for both 100 mcg and 250 mcg. The sponsor-reported ANCOVA analyses list superiority comparisons against placebo, with p-values of 0.013, <0.001, and <0.001, respectively. Those p-values summarize evidence under the sponsor’s analysis; they do not quantify the size or clinical importance of the differences.

The registry record does not state what size of FEV1 change would be clinically meaningful. The simple recalculations give estimates and confidence intervals from posted summary data, but they are unadjusted and do not replace the sponsor’s ANCOVA. The endpoint also represents a group average, so it does not show how every participant’s measurement changed or whether individual experiences were similar.

These findings do not establish how the treatment would compare in other populations, settings, or follow-up periods. The registered endpoint is measured through week 12, and the record does not provide longer-term results in the registry record for this analysis. The outcomes also cannot establish whether a change in FEV1 leads to a change in symptoms, daily functioning, or other outcomes not reported as results.

Safety counts are descriptive and limited to the adverse-event information reported. The observed event counts do not prove causation or rule out less common or later events. Interpretation should also account for the endpoint’s LOCF handling, incomplete reporting of the ANCOVA model and multiplicity procedures, and the discrepancy flagged between sponsor analyses and recalculations. The result is best read as a registry-reported comparison with statistical and reporting limitations, not as standalone clinical guidance.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares three doses with a placebo group using a continuous lung-function endpoint and reports both group summaries and sponsor-reported ANCOVA p-values. The arm means and standard deviations make the scale and variability of the observed changes visible. The dose-by-dose structure also makes clear why one should not collapse all active-treatment groups into a single comparison without a prespecified reason.

The record illustrates an important distinction between a model-based trial analysis and a recalculation from summary statistics. The posted ANCOVA analyses are the sponsor’s inferential results, while the recalculated mean differences and intervals provide a simpler unadjusted view. Their roles differ, and the discrepancy flag reinforces why analysis method and reporting detail matter. A p-value alone cannot describe effect magnitude, and an unadjusted interval should not be mistaken for an adjusted model result.

It also highlights the importance of outcome populations and missing-data methods. The primary endpoint description refers to a full analysis set, specifies endpoint counts based on observed baseline and end-of-treatment values, and describes LOCF imputation. Without further detail on exclusions, missingness, or sensitivity analyses, a reader cannot fully judge how robust the endpoint estimates are to those decisions.

Finally, planning calculations based on observed effects can help illustrate how required sample size changes with the target effect, but they do not reveal the trial’s original design rationale. The record’s absent multiplicity and model details limit the strength of independent statistical assessment, even though the broad direction of the posted group means is straightforward to describe.

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 limitations are specific to the registry information for this study. The sponsor-reported primary analyses include ANCOVA methods and p-values, but not adjusted effect estimates, confidence intervals, covariate details, or model diagnostics. That prevents readers from fully assessing the size and precision of the sponsor’s adjusted comparisons. The unadjusted recalculations offer a separate summary-based perspective but cannot fill those reporting gaps.

The record marks a discrepancy between the sponsor’s analysis and the recalculation. This makes it especially important to treat the sponsor’s own analysis as the primary inferential result and to label recalculated estimates as unadjusted. The registry does not explain the discrepancy in further detail.

Multiplicity procedures are not reported despite several dose comparisons and secondary outcomes. The endpoint description identifies LOCF imputation and notes that 2 subjects had no post-dose FEV1 assessment, but does not give a full account of missingness or sensitivity analyses. The relationship between the stated full analysis set and the endpoint counts could be clearer.

The registry also does not report the original sample-size rationale, a clinically meaningful FEV1 threshold, or detailed protocol and analysis-plan information. The posted results cover the stated baseline-to-week-12 endpoint; longer-term results are not reported in this record. Safety summaries provide event counts but cannot, on their own, establish causality or characterize all possible risks. These limitations reflect what the registry reports and should not be taken as evidence that unreported procedures or analyses did not occur.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Clinical Study to Evaluate the Efficacy of VR506 Using a New Inhaler for the Treatment of Asthma — NCT01472757.
• Registry record last updated 2020-04-21; status last verified 2020-04.
• Results first posted 2020-04-21.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry identifies a completed randomized, quadruple-masked, parallel-group study of VR506 delivered through a new inhaler in adolescents and adults with asthma. Enrollment was 374. The primary outcome was mean change in morning pre-dose FEV1 from baseline to week 12, reported in liters, with placebo compared against VR506 50 mcg, 100 mcg, and 250 mcg.

The sponsor-reported ANCOVA analyses list superiority comparisons for all three doses versus placebo. The registry provides p-values but not adjusted effect estimates or confidence intervals. Summary-based recalculations show positive unadjusted mean differences, and the record flags a discrepancy; the sponsor’s own analysis takes precedence. The endpoint description reports LOCF handling of missing post-baseline visits and notes that 2 subjects had no post-dose FEV1 assessment. Multiplicity procedures and the original sample-size justification are not reported in the registry record.