Cardiovascular Function in COPD Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cardiovascular Function in COPD Patients (NCT03055988), a randomized phase 4 study. The primary outcome is Change From Baseline in Left Ventricular End Diastolic Volume Index (LVEDVI) in the 6th Week of Treatment.

2. Clinical Question

3. Trial Design

The registry describes a completed phase 4 randomized, double-blind, double-dummy, active-controlled, two-period crossover study. Its official title identifies the two inhaled fixed-dose combinations: tiotropium plus olodaterol, delivered by Respimat, and fluticasone propionate plus salmeterol, delivered by Accuhaler. Treatment periods were 6 weeks. Because the design was crossover, participants were assigned to treatment sequences and the comparison concerns the two treatments within the study's crossover framework, rather than a conventional parallel-group comparison. The registry record does not report the sequence allocation details or a washout period.

The registry lists enrollment as 76 and the study status as completed. The primary endpoint's posted arm summaries each include 59 observations; this does not change the registry's enrollment figure, and the record does not explain the difference in those counts. Secondary endpoint summaries use different counts, as reflected in the posted results. The primary population is described as a full analysis set (FAS), requiring a baseline measurement and at least one post-baseline measurement. A nested full analysis set excluding exacerbations (FAS-EE) excludes data from patients who had an exacerbation during treatment. The registry's primary result reports a mixed model repeated measures analysis. Further details of the sequence, missing-data handling, model covariates, and original design assumptions 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.

Before assignment: All patients were screened for eligibility to participate in the trial. Patients attended specialist sites which would then ensured that all patients met all inclusion/exclusion criteria. Patients were not to be randomized to trial treatment if any one of the specific entry criteria were not met.

Period 1

Reasons for not completing this period:

Period 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FullAnalysisSet (FAS)ExcludingExacerbation (FAS-EE) nested within FAS and data from patients who had an exacerbation during treatments were excluded from this set. FAS nested within treated set and included patients who had baseline measurement and at least one post-baseline measurement for primary or secondary endpoints. (Including available data)

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.

Population: The treated set (TS): TS is nested within the randomised set and includes all patients who were dispensed study medication and were documented to have taken any dose of study medication. RS includes all patients who signed informed consent form and were also randomised, regardless whether the patient was treated with study medication or not.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Left Ventricular End Diastolic Volume Index (LVEDVI) in the 6th Week of Treatment, measured over Baseline and 6 weeks.

The primary endpoint was change from baseline in left ventricular end diastolic volume index (LVEDVI) in the 6th week of treatment. LVEDVI is the left ventricular end diastolic volume divided by body surface area, and is reported in millilitres per square metre. The registry describes baseline as the assessment performed in a week prior to Visit 2 (Day 1). Change was calculated from the baseline value to the value obtained in a week prior to Visits 3 and 4, at the end of each treatment period.

This endpoint was used to assess a cardiac imaging measure in a study exploring cardiovascular function in people with COPD. The study objective specifically included exploring reversal of left ventricular diastolic dysfunction, assessed with cardiac magnetic resonance imaging. LVEDVI quantifies ventricular volume adjusted for body size; it is not itself a direct measure of every aspect of cardiac function. The registry does not report a threshold for a clinically important change or a rationale for selecting this endpoint over other cardiac measures. Accordingly, the result should be read as a comparison of changes in this defined measure, not as a complete assessment of cardiovascular status.

7. Results Posted in the Registry

• Tiotropium + Olodaterol FDC (T+O 5/5): mean 2.32 versus 2.85 on control; difference -0.54 (95% CI -3.69 to 2.61), standardized effect d = -0.06; z-test p = 0.738.

8. Secondary Efficacy Endpoints

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

Change From Baseline in Aortic Distensibility After 6 Weeks of Treatment

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Tiotropium + Olodaterol FDC (T+O 5/5): mean -0.01 versus -0.01 on control; difference 0.00 (95% CI -0.10 to 0.10), standardized effect d = 0.00; z-test p = 0.984.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tiotropium + Olodaterol FDC (T+O 5/5) and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Pulmonary Artery Pulsatility After 6 Weeks of Treatment

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Tiotropium + Olodaterol FDC (T+O 5/5): mean 1.10 versus -0.17 on control; difference 1.28 (95% CI -3.81 to 6.37), standardized effect d = 0.09; z-test p = 0.622.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tiotropium + Olodaterol FDC (T+O 5/5) and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Central Systolic Pressure After 6 Weeks of Treatment

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Tiotropium + Olodaterol FDC (T+O 5/5): mean 2.27 versus 0.20 on control; difference 2.07 (95% CI -2.25 to 6.39), standardized effect d = 0.17; z-test p = 0.348.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tiotropium + Olodaterol FDC (T+O 5/5) and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover cardiovascular measures, lung volumes, and post-dose spirometry. Across the available analyses, the estimates do not form a consistent pattern of clear, precise separation between treatments: reported confidence intervals include zero, and the recalculated unadjusted p-values are not small. The overall secondary picture is therefore compatible with uncertainty about comparative effects, rather than a coherent set of results that independently confirms a treatment difference.

These secondary measures relate to the primary result by extending the study's exploratory assessment beyond LVEDVI. They address arterial stiffness and pressure measures as well as hyperinflation and spirometry, but they do not change the interpretation of the primary endpoint. A collection of secondary outcomes can provide context, yet does not establish a result on the primary endpoint or on patient-important outcomes not measured in the record.

Multiplicity reduces the weight that should be placed on any single secondary finding when several outcomes are tested. If each is interpreted without adjustment, the chance of chance findings across the collection increases. The registry record does not report a multiplicity procedure or a prespecified hierarchy for secondary outcomes. Thus, their results are best treated as exploratory signals requiring confirmation, not as independent confirmatory claims. The registry lists 8 secondary outcomes, while the posted analyses cover only some of them; outcomes not included in the posted analyses are not reported in the registry record with results.

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

• Change From Baseline in Aortic Distensibility After 6 Weeks of Treatment
• Change From Baseline in Pulmonary Artery Pulsatility After 6 Weeks of Treatment
• Change From Baseline in Central Systolic Pressure After 6 Weeks of Treatment
• Change From Baseline in Pulse Pressure After 6 Weeks of Treatment
• Change From Baseline in Aortic Augmentation Index After 6 Weeks of Treatment
• Change From Baseline in Functional Residual Capacity Body Plethysmography (FRCpleth) % Predicted After 6 Weeks of Treatment
• Change From Baseline in 1.5 Hour Post Dose Forced Expiratory Volume in 1st Second (FEV1) After 6 Weeks of Treatment
• Change From Baseline in 1.5 Hour Post Dose Forced Vital Capacity (FVC) After 6 Weeks of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numerical measure of change in LVEDVI. The registry reports least-squares means and standard errors for the treatment summaries. A least-squares mean is a model-based mean, adjusted for terms included in the analysis. The registry identifies the sponsor's method as mixed model repeated measures (MMRM), but the detailed model specification and covariates are not reported in the registry record. Standard error describes the precision of an estimated mean; it is not the same quantity as the variability of individual measurements.

What does the crossover design change?

In a crossover trial, participants receive treatments in different periods, so each participant can contribute information under more than one treatment. This can help account for stable differences between people when comparing treatment responses. It also makes the analysis dependent on features such as treatment sequence, period effects, and possible carryover from one period to another. The registry describes two treatment periods but does not report sequence details or a washout period. The posted sponsor method, MMRM, is the method to consult for the primary comparison; the full model details are not reported in the registry record.

The simple recalculation is different in purpose. It uses the posted group summary statistics to form an unadjusted comparison and approximate uncertainty. It is not a substitute for the sponsor's adjusted repeated-measures analysis and does not reproduce the crossover structure, participant-level pairing, or any model adjustments. In particular, the posted arm summaries provide standard errors, and the recalculation uses an approximate standard deviation. This approximation is useful as a transparent check on the scale and direction of the reported result, but should not take precedence over the registry's sponsor analysis.

How should the confidence interval and p-value be read?

A confidence interval gives a range of estimates compatible with the observed data under the model and its assumptions. For the primary result, the 95% interval spans negative and positive values and includes zero. That means the result does not distinguish a difference from no difference at conventional significance thresholds. It does not show that every value in the interval is equally plausible, and it is not a probability statement about the true effect. The p-value of 0.633 is consistent with the interval's inclusion of zero. It is not a measure of treatment benefit, clinical importance, or the probability that the null hypothesis is true.

MMRM is a general approach for repeated measurements, often used to model outcomes across time and account for correlation among measurements from the same participant. In a crossover context, model terms can represent aspects such as treatment and period, but the exact terms used in this trial are not reported in the registry record. The method's assumptions matter: misspecified mean structure or covariance, and assumptions about unobserved measurements, can affect estimates and uncertainty. The registry record does not describe diagnostic checks or sensitivity analyses.

Why can over-dispersion matter in general?

As a general statistical point, over-dispersion occurs when observed variation is greater than a model expects. If a model understates variability, standard errors may be too small and confidence intervals too narrow, making evidence appear more precise than it is. If variability is modeled adequately, uncertainty is better represented. This trial's primary endpoint is continuous, and the registry does not report an over-dispersion analysis; this concept is not a claim about the posted LVEDVI results.

The primary population description includes a full analysis set requiring baseline and at least one post-baseline measurement, and a nested set excluding data from participants who experienced an exacerbation during treatment. These definitions indicate that analysis availability and exacerbations were relevant to population selection. The registry does not report how many observations were missing, the reasons for missingness, or the method used to handle missing outcomes. Those omissions limit independent assessment of the assumptions underlying the repeated-measures analysis.

The secondary outcomes are also continuous measures, and the registry posts separate analyses for them. Multiple outcome testing raises a general multiplicity concern: when many hypotheses are assessed, the chance of at least one apparently notable result can increase. No multiplicity adjustment is reported in the registry record. Secondary p-values should therefore be interpreted as exploratory and not as isolated confirmatory evidence. Sample-size planning illustrations based on observed effects are a separate exercise and do not provide evidence about the trial's original sample-size justification or its achieved power.

11. Confidence Intervals and Precision

The sponsor's primary 95% confidence interval extends from -2.779 to 1.705 for the adjusted mean difference in LVEDVI change. Since zero lies within the interval, the data are compatible with no treatment difference under the analysis, as well as with differences in either direction. The interval is not narrow enough to identify a precise direction or magnitude. The registry does not report a clinical-importance threshold, so the interval cannot be classified against a stated threshold for meaningful change.

The unadjusted recalculation has a 95% interval from -3.688 to 2.612. This is wider than the sponsor interval, and it arises from a different, approximate calculation. It should not be treated as the main result or as a replacement for the crossover model. Both intervals include zero, but their different widths illustrate why an adjusted repeated-measures analysis and a summary-statistic recalculation need not have the same precision.

Confidence intervals express uncertainty in an estimate under the analysis assumptions; they do not describe the range of individual participant responses. The registry does not report the distribution of individual changes, the correlation between treatment-period measurements, or sensitivity analyses for missing data. Those details would help readers assess how much confidence to place in the model-based precision. The posted result therefore supports a cautious statement: the estimated difference is close to zero, but the uncertainty does not establish equivalence or exclude all potentially relevant differences.

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 table and curve are planning illustrations based on the observed effect, not the study's original design assumptions. For these continuous outcomes, the figures are participants per arm, not total events. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning effect is the stated fraction of the observed effect. The registry record does not report the trial's original sample-size justification or design assumptions.

The 80% power column describes the number of participants per arm estimated to give an 80% chance of detecting the specified effect under those planning assumptions, if that effect and the model assumptions were correct. The 90% column uses a higher target chance of detection under the same framework. These are design targets, not probabilities that the reported finding is true. The calculations are planning illustrations based on an effect estimated in this study; they are not observed power.

Rows for planning for 100%, 75%, and 50% of the observed effect show how the assumed target effect changes the planning requirement. A smaller effect is harder to distinguish from random variation, so planning for a smaller effect requires more participants. In particular, estimates based on a very small observed effect can yield very large planning figures; these should be understood as consequences of the specified assumptions, not as recommendations or a reconstruction of the actual study design. Because this was a crossover study and the illustrations use a normal approximation with equal allocation, they do not by themselves capture all features of the sponsor's repeated-measures analysis.

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 = -0.538; pooled standard deviation σ = 8.730.
2. n = 2 × (1.96 + 0.842)² × 8.730² / -0.538² = 4,133.0, rounded up to 4,133 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 <- -0.538                      # observed difference in means
sigma <- 8.72962298727728                     # 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(3055988)
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 = 4,133 (80% power), 5,533 (90% power)
 75% of observed effect: n per arm = 7,348 (80% power), 9,837 (90% power)
 50% of observed effect: n per arm = 16,532 (80% power), 22,132 (90% power)
power.t.test: 4133.9 
Simulated power at n = 4,133 per arm: 0.794 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry's sponsor-reported primary analysis is an MMRM comparison with an adjusted mean difference of -0.537, a 95% confidence interval from -2.779 to 1.705, and p = 0.633. This is the study's reported analysis and should take precedence over the simple recalculation. The recalculated unadjusted estimate is -0.538, with a 95% confidence interval from -3.688 to 2.612 and p = 0.738. The estimates are close, while the intervals and p-values differ.

That difference is expected because the recalculation uses posted summary statistics and approximate variability, whereas the sponsor analysis uses a repeated-measures model. The simple calculation cannot reproduce participant-level pairing, crossover periods, or model adjustments. The registry lists no discrepancy flag. The sponsor result therefore remains the more relevant estimate for interpreting the trial's stated primary analysis; the recalculation is a check on the broad scale and direction, not an independent analysis of the original data.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary endpoint and multiple secondary outcomes. Testing several outcomes raises multiplicity: even when no treatment effect exists, multiple statistical tests can produce an apparently notable result by chance. Methods such as prespecified testing hierarchies or adjustments can address this issue, but a multiplicity strategy is not reported in the registry record. The secondary findings should therefore be interpreted as exploratory, and their p-values should not be read as if each were the sole planned test.

The primary population description identifies a full analysis set requiring a baseline measure and at least one post-baseline measure. It also describes a nested FAS-EE population that excludes data from patients who had an exacerbation during treatment. The registry record does not report the primary result separately for both populations in the information available for this analysis, nor does it describe which population generated the posted primary estimate in enough detail to resolve that question. The rationale and consequences of excluding exacerbation-period data are also not fully reported.

Missing-data details are limited. The registry record does not report the number or reasons for missing outcome measurements, assumptions about why data were missing, or sensitivity analyses evaluating alternative assumptions. This matters because repeated-measures models rely on assumptions about the observed and unobserved data. Without these details, readers cannot fully assess the robustness of the primary estimate to missing observations.

The original sample-size justification, interim analysis plan, and full statistical analysis plan are not reported in the registry record. The planning illustrations based on observed effects do not fill that gap. The study's design and posted primary analysis can be described, but the record does not support claims about how the original target enrollment was chosen, whether interim looks were planned, or whether the analysis followed an unreported prespecified strategy.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: ligament rupture (1.4%), osteoporotic fracture (1.4%), chronic obstructive pulmonary disease (1.4%).

The registry reports serious adverse events among groups at risk of 70 for F+S and 74 for T+O. Serious adverse events affected 0 in the F+S group and 2 in the T+O group. The registry also reports other adverse events affecting 7 in the F+S group and 13 in the T+O group. Deaths were 0 in each group. These are descriptive event summaries, not a formal comparative safety analysis.

The serious-event terms listed include ligament rupture, osteoporotic fracture, and chronic obstructive pulmonary disease, each reported as 1.4%. The registry information presented does not link those terms to a specific treatment group in this listing, so they should not be attributed to one. Event counts alone do not establish a treatment-related cause or a difference in risk. The record does not provide a statistical comparison of adverse-event rates, detail on event timing, or a full account of severity and relatedness. The group counts should be read in the context of the registry's reported at-risk denominators, not as evidence that one regimen is safer.

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

The central statistical finding is an imprecise comparison of change in LVEDVI after 6 weeks of treatment. The sponsor's adjusted estimate is -0.537, with a 95% confidence interval from -2.779 to 1.705 and p = 0.633. Because the interval includes zero and allows estimates in either direction, the result does not establish a difference between the two treatments on the primary measure. It also does not prove that their effects are identical. Equivalence would require an appropriate design and a prespecified margin, neither of which is reported in the registry record.

The endpoint is a normalized cardiac volume measure assessed by imaging. It does not encompass all cardiovascular function, COPD symptoms, exacerbations, or long-term clinical events. The study also explored arterial stiffness, hyperinflation, and spirometry, but the registry record does not establish effects on outcomes beyond those measured and reported. The 6-week treatment periods do not support conclusions about longer-term comparative outcomes.

The randomized, double-blind crossover design offers a structured comparison of the two active treatments. However, the registry record does not report all details needed to evaluate sequence, carryover, missing-data assumptions, or sensitivity of the findings to analysis choices. The secondary results add exploratory context but are subject to multiplicity and should not be treated as definitive evidence. Overall, the posted data describe an uncertain treatment contrast on the primary endpoint, not proof of benefit, harm, or equivalence.

18. Why This Trial Matters Statistically

This study illustrates why interpreting a treatment comparison requires more than looking at the point estimate or p-value. The primary estimate is close to zero, but its confidence interval is broad enough to include differences in either direction. That distinction matters: a result that does not establish a difference is not the same as a result that demonstrates no difference. Precision, endpoint meaning, and design all shape what the data can support.

The crossover structure also highlights the importance of matching an analysis to the study design. The sponsor reports an MMRM analysis, while a simple recalculation from arm summaries offers only an approximate, unadjusted check. Similar point estimates do not make those analyses interchangeable. The sponsor's model-based result is the appropriate primary reference, and its assumptions and details matter for interpretation.

Finally, the registry lists several secondary outcomes, creating a multiplicity issue, and offers limited information about missing data and the original statistical plan. These features distinguish exploratory evidence from a confirmatory conclusion. The record is informative about the measured endpoint and the analysis reported, but its limits should remain visible when interpreting the breadth and precision of the findings.

19. Limitations

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

Several trial-specific limitations constrain interpretation. The study is described as exploratory, and the registry record does not report a clinical-importance threshold for LVEDVI or a prespecified equivalence margin. The primary estimate therefore cannot be translated into a judgment about clinically meaningful benefit or equivalence from the posted information alone.

The primary result is reported from an MMRM analysis, but model covariates, covariance structure, treatment sequence terms, and sensitivity analyses are not reported in the registry record. The trial is a crossover study, yet sequence allocation details and a washout period are not reported. These details would help readers assess period and carryover considerations. The simple recalculation is approximate and does not recreate the participant-level crossover analysis.

The primary arm summaries each report 59 observations, while registry enrollment is 76; the record does not explain this difference. Secondary outcomes also have varying reported counts. The FAS and FAS-EE descriptions identify analysis-population rules, but detailed missing-data counts, reasons, and sensitivity analyses are not reported. The original sample-size justification and interim analysis plan are also not reported in the registry record.

Multiple secondary measures were assessed, and no multiplicity adjustment is reported. Their results should be considered exploratory. The posted endpoint set focuses on measures over 6 weeks and does not establish long-term effects or comparative effects on clinical outcomes not listed as measured outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Cardiovascular Function in COPD Patients — NCT03055988.
• 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.

23. Record Summary

NCT03055988 is a completed phase 4 randomized, double-blind, double-dummy, active-controlled, two-period crossover study in people with COPD. It compared tiotropium plus olodaterol with fluticasone propionate plus salmeterol over 6-week treatment periods. Registry enrollment was 76.

The primary endpoint was change from baseline in LVEDVI at the 6th week of treatment. The sponsor-reported MMRM analysis estimated an adjusted mean difference of -0.537, with a 95% confidence interval from -2.779 to 1.705 and p = 0.633. The interval includes zero and does not establish a treatment difference. The registry also lists secondary cardiovascular and respiratory measures and adverse-event summaries. Multiplicity, missing-data methods, original sample-size rationale, and several crossover analysis details are not reported in the registry record.