Evaluation of Umeclidinium Bromide in Combination With Fluticasone Furoate in COPD Subjects With an Asthmatic Component: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of Umeclidinium Bromide in Combination With Fluticasone Furoate in COPD Subjects With an Asthmatic Component (NCT02164539), a randomized phase 2 study. The primary outcome is Change From Baseline in Clinic Trough Forced Expiratory Volume in One Second (FEV1) at the End of Treatment Phase A (Visit 6/Day 29).

2. Clinical Question

The study asked whether adding umeclidinium bromide (UMEC) to fluticasone furoate (FF) was associated with a different change in clinic trough forced expiratory volume in one second (FEV1) than FF alone in COPD participants with an asthmatic component. It also included a comparison with FF/vilanterol (VI). The primary endpoint was the change from baseline in trough FEV1 at the end of Treatment Phase A.

These questions concern measured changes and estimated differences in this trial. The registry record does not report enough information to establish how the original study's sample size or full statistical plan was determined.

3. Trial Design

This was a completed phase 2 study with randomized allocation, double masking and a parallel-group model. The registry lists enrollment of 338 participants. The study started on 2014-07-01 and primary completion was 2015-07-01. GlaxoSmithKline is listed as the sponsor.

The brief summary describes a dose-response evaluation of four FF/UMEC doses against FF monotherapy, with FF/UMEC treatments also compared with once-daily FF/VI. Before Treatment Phase A, eligible participants entered a 4-week run-in and received fluticasone propionate/salmeterol. Participants were then randomized to Treatment Phase A. The registry lists the Phase A arms for the primary endpoint as FF 100 µg, FF/UMEC 100/15.6 µg, FF/UMEC 100/62.5 µg, FF/UMEC 100/125 µg, FF/UMEC 100/250 µg and FF/VI 100/25 µg.

Later treatment phases applied to participants completing earlier phases. In Treatment Phase B, completers were randomized to FF/UMEC 100/250 µg or FF/UMEC/VI 100/250/25 µg for 1 week. In Treatment Phase C, completers were randomized to continue the Phase B treatment or receive the same treatment without UMEC for 1 week. These later phases mean not all treatment and safety group sizes correspond to the primary Phase A groups.

The registry record does not report the original sample-size justification or the details of the randomization sequence and masking procedures. It also does not report a full protocol description beyond the posted treatment information.

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: Participants on inhaled corticosteroid therapy over the previous 12 weeks, including a stable dose during the 4 weeks prior to Visit 0, entered the 4-week run-in period on open-label fluticasone propionate 250 microgram (µg) and salmeterol 50 µg combination. Eligible par. were stratified by smoking status, age and randomized to Treatment Phase A.

Only the first 6 of 7 groups are shown.

Treatment Phase A (4 Weeks)

Reasons for not completing this period:

Treatment Phase B (1 Week)

Reasons for not completing this period:

Treatment Phase C (1 Week)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT Population. Only those participants available at the specified time point were analyzed.

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.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Clinic Trough Forced Expiratory Volume in One Second (FEV1) at the End of Treatment Phase A (Visit 6/Day 29), measured over Baseline and Day 29.

The primary endpoint was change from baseline in clinic trough FEV1 at the end of Treatment Phase A, specified as Visit 6/Day 29. FEV1 is the volume of air exhaled in the first second of a forced expiration. It is a continuous measurement, and the registry reports its mean change in liters with standard deviations.

The endpoint was based on spirometry performed in the morning at scheduled visits. Trough FEV1 for the endpoint was the acceptable or borderline acceptable value at Visit 6, approximately 24 hours after morning dosing on Visit 5. Baseline was the last acceptable or borderline acceptable value before randomization, taken at Visit 2 pre-bronchodilator or Visit 3 pre-dose. The timeframe is listed as baseline and Day 29.

Using a continuous measurement retains information about the magnitude of change rather than reducing each participant's result to a category. A mean difference between treatment arms estimates the contrast in average change, while the spread of participant measurements indicates how variable individual changes were. This is a general statistical rationale for continuous endpoints; it does not itself establish the clinical importance of a particular difference.

The registry says the primary population was the ITT population, defined there as randomized participants who received at least one dose of randomized study medication in the treatment period. Only participants available at the specified time point were analyzed. The record does not report how missing endpoint measurements were handled beyond that statement.

7. Results Posted in the Registry

• FF/UMEC 100/15.6 µg: mean 0.15 versus 0.05 on control; difference 0.10 (95% CI -0.02 to 0.22), standardized effect d = 0.37; z-test p = 0.099.
• FF/UMEC 100/62.5 µg: mean 0.19 versus 0.05 on control; difference 0.15 (95% CI 0.03 to 0.26), standardized effect d = 0.56; z-test p = 0.014.
• FF/UMEC 100/125 µg: mean 0.17 versus 0.05 on control; difference 0.13 (95% CI 0.01 to 0.25), standardized effect d = 0.47; z-test p = 0.036.
• FF/UMEC 100/250 µg: mean 0.14 versus 0.05 on control; difference 0.10 (95% CI -0.02 to 0.21), standardized effect d = 0.31; z-test p = 0.106.

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 Baseline in Rescue Medication Use at the End of Treatment Phase A

• 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:
  • FF/UMEC 100/15.6 µg: mean -0.40 versus 0.60 on control; difference -1.00 (95% CI -1.80 to -0.20), standardized effect d = -0.54; z-test p = 0.015.
  • FF/UMEC 100/62.5 µg: mean -0.50 versus 0.60 on control; difference -1.10 (95% CI -1.90 to -0.30), standardized effect d = -0.60; z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for FF/UMEC 100/15.6 µg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for FF/UMEC 100/62.5 µg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Mean Change From Baseline in E-RS Total Scores at the End of Treatment Phase A

• 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:
  • FF/UMEC 100/15.6 µg: mean -2.60 versus 0.50 on control; difference -3.10 (95% CI -4.61 to -1.59), standardized effect d = -0.89; z-test p = <0.001.
  • FF/UMEC 100/62.5 µg: mean -2.50 versus 0.50 on control; difference -3.00 (95% CI -4.52 to -1.48), standardized effect d = -0.87; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for FF/UMEC 100/15.6 µg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for FF/UMEC 100/62.5 µg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Daily Morning (AM) PEF (Pre-dose and Pre-rescue Bronchodilator) Measured at Home and Averaged Over the Last 21 Days of Treatment Phase A

• 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:
  • FF/UMEC 100/15.6 µg: mean 3.90 versus -14.20 on control; difference 18.10 (95% CI 5.18 to 31.02), standardized effect d = 0.61; z-test p = 0.006.
  • FF/UMEC 100/62.5 µg: mean 7.60 versus -14.20 on control; difference 21.80 (95% CI 8.80 to 34.80), standardized effect d = 0.74; z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for FF/UMEC 100/15.6 µg 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 FF/UMEC 100/62.5 µg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several kinds of measurement: rescue medication use, respiratory symptom scores, daily morning peak expiratory flow and clinic FEV1 measurements after treatment. Across the posted results, the early FF/UMEC doses generally have more favorable changes than FF alone on the listed rescue-medication, symptom and home peak-flow outcomes. The FF/UMEC arms also show positive mean changes in the listed clinic FEV1 measures. The degree and direction of contrast vary by outcome and dose; the secondary findings do not form a single uniform pattern.

These outcomes provide context around the primary lung-function endpoint because they measure related but distinct aspects of the treatment period. Agreement across different measures can make the overall pattern of observations more informative, but secondary endpoints cannot be treated as independent confirmation of the primary result. Their measurement scales, timing and analysis populations differ, and the registry record does not provide a single integrated analysis across them.

The sponsor's posted secondary analyses include ANCOVA comparisons for selected arms. Recalculated unadjusted comparisons are not interchangeable with those adjusted analyses. The registry also lists six outcome measures and 30 analyses overall, while only five secondary outcome summaries are posted in the record. The complete set of prespecified and conducted analyses is not described.

Unadjusted secondary results carry less weight because multiple outcomes and comparisons create more opportunities for chance findings, and the record does not report a multiplicity adjustment strategy. Some outcomes also have different participant counts, and missing-data handling is not detailed. The secondary pattern is therefore useful as supporting descriptive context, but it should not override the sponsor's primary analysis or be interpreted as a set of definitive independent tests.

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

• Mean Change From Baseline in Rescue Medication Use at the End of Treatment Phase A
• Mean Change From Baseline in E-RS Total Scores at the End of Treatment Phase A
• Change From Baseline in Daily Morning (AM) PEF (Pre-dose and Pre-rescue Bronchodilator) Measured at Home and Averaged Over the Last 21 Days of Treatment Phase A
• Change From Trough in Clinic Forced Expiratory Volume (FEV1) at 3 Hours Post-study Treatment at Visit 5/Day 28
• Change in Clinic FEV1 Following 2 Puffs of Albuterol/Salbutamol Given 3 Hours Post-study Treatment Dose at Visit 5/Day 28

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, so the main summaries are means and standard deviations. A mean describes the average change in a group; the standard deviation describes the spread of participant-level changes around that average. These quantities answer different questions: a mean difference describes the contrast in group averages, while a standard deviation helps convey how variable the responses were.

What does a mean difference represent?

A mean difference compares the average change in one treatment arm with the average change in the reference arm. For example, the registry's sponsor analysis describes a net mean difference for FF/UMEC versus FF. Positive values in the posted primary results indicate a larger average change in the FF/UMEC arm than in the FF arm, according to the direction used for this endpoint. The difference is an estimate, not a count of participants who improved and not a statement about the importance of the change.

The recalculated comparisons are simple unadjusted comparisons based on posted arm-level summary statistics. They are not the same as a model that adjusts for baseline values or other covariates. The registry's reported primary analysis method is a final step dose-response model. For secondary outcomes, the listed sponsor method is ANCOVA. ANCOVA is a general approach for comparing outcome means while accounting for covariates; however, the registry record does not fully specify the covariates or model details used in these analyses.

How should p-values be read?

A p-value describes how compatible the observed data are with a specified null model, assuming that model and its assumptions are appropriate. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical relevance of an effect. The recalculated p-values are explicitly unadjusted. The registry reports sponsor p-values for its own analyses, but the multiplicity handling for the family of dose and endpoint comparisons is not reported in the registry record.

The sponsor's primary model reports p = 0.024 for the FF/UMEC comparisons and p = 0.152 for the FF/VI comparison. The recalculated pairwise values differ. Because the record flags a discrepancy, the sponsor's own analysis takes precedence; the recalculations should be interpreted as unadjusted checks rather than alternate sponsor findings.

What is the role of the confidence interval?

A confidence interval describes a range of values reasonably compatible with the data and the analysis method, under repeated use of that method. Wider intervals indicate less precision, while narrower intervals indicate more precision. If a mean-difference interval includes zero, the data remain compatible with no average difference under that analysis. If it excludes zero, the interval indicates a nonzero contrast under the same assumptions. Neither result alone answers whether the magnitude matters clinically.

The sponsor's reported primary model gives a 95% confidence interval from 0.014 to 0.193 for the FF/UMEC contrasts, and from -0.027 to 0.172 for FF/VI. The recalculated intervals are also reported as unadjusted estimates, but some bounds are recorded with more than three decimal places and are not repeated in this narrative. The distinction between model-based and unadjusted estimates matters because their assumptions and precision can differ.

Why can dose-response modeling differ from pairwise comparisons?

A dose-response model can estimate a pattern across multiple dose groups rather than treating each dose comparison as entirely separate. The registry labels the primary method a final step dose-response model but does not report the model equation, step-selection procedure, or the exact estimand. Those unreported details prevent a full reconstruction of the sponsor analysis from the registry summary alone. In particular, the repeated 0.103 estimate for all four FF/UMEC comparisons should not be read as evidence that the observed arm means were identical; the arm-level means differ.

Pairwise recalculation instead contrasts each arm's posted mean with the reference mean using the summary statistics. It does not reproduce a dose-response model. Differences between those approaches can arise from the method and assumptions used, and the discrepancy is explicitly flagged in the record. Without further model details, it is not appropriate to assert a specific reason for the difference.

What does over-dispersion mean in general?

Over-dispersion is a general statistical concern when observed variability is greater than a model expects. If a model underestimates variability, standard errors can be too small and confidence intervals too narrow. It is relevant to count or event models in particular, whereas this primary outcome is continuous and its posted summaries use means and standard deviations. The registry does not report an over-dispersion assessment for the primary analysis, so no claim about its presence or absence can be made.

Finally, the reported primary population includes randomized participants who received at least one dose, with only those available at the specified time point analyzed. This population definition and availability rule are important to interpretation. The registry does not report a detailed missing-data method, sensitivity analyses, or whether all randomized participants contributed to each endpoint estimate.

11. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval: a narrower interval indicates a more precisely estimated contrast, while a wider interval allows a broader range of values. Precision depends on factors such as sample size and variability. The primary arm sizes range from 39.0 to 83.0, and the observed standard deviations vary across arms. These features help explain why estimates should be read with their intervals rather than in isolation.

For the sponsor's primary dose-response analysis, the FF/UMEC estimate is 0.103 liters with a 95% confidence interval from 0.014 to 0.193. The FF/VI estimate is 0.073 liters with a 95% confidence interval from -0.027 to 0.172. The first interval excludes zero; the second includes zero. This distinction describes uncertainty under the sponsor's reported model, not the probability that a treatment effect is true and not the clinical importance of either estimate.

The recalculated unadjusted intervals differ from the sponsor intervals. For example, the recalculated FF/UMEC 100/15.6 µg interval crosses zero, while the recalculated intervals for FF/UMEC 100/62.5 µg and FF/UMEC 100/125 µg do not. This illustrates why the estimation method matters. Given the recorded discrepancy, the sponsor analysis takes precedence over the simple recalculation.

Intervals do not account for every source of uncertainty. Multiplicity, missing data, the model's assumptions and the selection of analyses may affect how results should be interpreted. The registry record does not report all those details. Confidence intervals are therefore best read as a description of precision for the stated analysis, not as a complete account of uncertainty.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are hypothetical illustrations based on the observed effect and are not the study's original sample-size calculations. They are expressed as participants per arm, not total events. The registry's planning 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. The original trial's design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for an analysis with an 80% chance of detecting the specified effect if that effect were the true one, under the planning assumptions. The 90% power column gives the corresponding planning number for a higher chance of detection. These are design calculations, not properties measured after the trial. This is not observed power.

Each effect scenario is anchored to the observed contrast, then considers planning for 100%, 75% or 50% of that observed effect. Smaller effects are harder to distinguish from random variation, so the required number of participants per arm increases as the target effect becomes smaller. For instance, for the recalculated FF/UMEC 100/62.5 µg contrast, the planning figures rise from 51 participants per arm for 80% power at 100% of the observed effect to 204 participants per arm at 50% of the observed effect. These numbers illustrate sensitivity to the assumed effect size; they are not evidence that the original study was designed using those assumptions.

The calculations do not reproduce the sponsor's dose-response analysis and should not be treated as a formal redesign recommendation. Their purpose is to show how planning requirements can change when the target effect is smaller or the desired power is higher.

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 = 0.099; pooled standard deviation σ = 0.267.
2. n = 2 × (1.96 + 0.842)² × 0.267² / 0.099² = 114.6, rounded up to 115 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 <- 0.099                      # observed difference in means
sigma <- 0.267440056456523                     # 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(2164539)
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 = 115 (80% power), 154 (90% power)
 75% of observed effect: n per arm = 204 (80% power), 273 (90% power)
 50% of observed effect: n per arm = 459 (80% power), 614 (90% power)
power.t.test: 115.5 
Simulated power at n = 115 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 sponsor's primary analysis is reported as a final step dose-response model. It gives a mean difference (net) of 0.103 liters, a 95% confidence interval from 0.014 to 0.193 and p = 0.024 for each listed FF/UMEC comparison with FF. For FF/VI versus FF, the final dose-response model gives 0.073 liters, a 95% confidence interval from -0.027 to 0.172 and p = 0.152.

The unadjusted recalculations use posted group means and variability to form pairwise contrasts. They differ from the sponsor's primary results, including in the estimate and the p-value for several comparisons. The registry record explicitly flags this discrepancy. Under that circumstance, the sponsor's own analysis takes precedence; the recalculations are best treated as a transparent descriptive check, not as a correction to the sponsor's result.

The record does not contain sufficient detail to recreate the dose-response model or explain why the same FF/UMEC estimate is repeated across dose comparisons. The dose-specific arm means remain distinct summaries, but they should not be substituted for the sponsor's model estimates. Interpretation should preserve this difference between the modeled result and the unadjusted recalculation.

15. Multiplicity, Missing Data and Analysis Populations

The study includes several treatment arms, multiple doses and several outcomes. Testing many contrasts can increase the chance of observing a small p-value by chance, even when no corresponding underlying difference exists. Statistical procedures that account for multiplicity can address this concern, but the registry record does not report whether or how the primary dose comparisons or secondary analyses were adjusted for multiplicity. The sponsor's model is described as a final step dose-response model, but the record does not give enough detail to determine how that model relates to the full family of comparisons.

There is a difference between the posted sponsor analyses and the simple unadjusted recalculations. The latter are not multiplicity adjusted. The discrepancy flag means the sponsor's own analysis takes precedence; the recalculations should not be presented as confirmatory results. The record does not identify a prespecified hierarchy or testing sequence for all endpoints.

The primary population is described as randomized participants who received at least one dose of randomized medication. The registry further states that only participants available at the specified time point were analyzed. This is an availability-based analysis statement, but the record does not explain what happened to participants with missing endpoint values, whether imputation was used, or whether sensitivity analyses assessed the impact of missingness.

Arm sizes differ across outcomes and treatment phases. This may reflect the specific analysis population and phase participation, but the registry does not provide a complete account of reasons for missing observations or exclusions. The original sample-size justification, interim analyses and full statistical analysis plan are also not reported in the registry record. These omissions limit assessment of analysis selection, missing-data sensitivity and the extent to which reported comparisons were prespecified.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypertensive crisis (0.5%), pneumonia (0.0%), transient ischaemic attack (tia) (0.0%), pulmonary embolism (pe) (0.0%).

The registry records serious adverse events in one of the listed groups: FF/UMEC 100/250 µg had 1 serious event among 210 participants at risk. The other listed groups each had 0 serious events recorded, with at-risk counts of 111 for FF 100 µg, 42 for FF/UMEC 100/15.6 µg, 40 for FF/UMEC 100/62.5 µg, 46 for FF/UMEC 100/125 µg, 146 for FF/VI 100/25 µg and 163 for FF/UMEC/VI 100/250/25 µg. Death counts are not reported in the registry record.

For other adverse events, the posted counts are 6 in the FF 100 µg group, 5 in FF/UMEC 100/15.6 µg, 4 in FF/UMEC 100/62.5 µg, 4 in FF/UMEC 100/125 µg, 5 in FF/UMEC 100/250 µg, 4 in FF/VI 100/25 µg and 0 in FF/UMEC/VI 100/250/25 µg. These counts should be read alongside the different numbers at risk and the different treatment-phase exposure groups.

The listed serious-event terms include hypertensive crisis at 0.5%, while pneumonia, transient ischaemic attack and pulmonary embolism are listed at 0.0%. Rare-event counts and percentages can be unstable, and these summaries do not establish comparative safety. The registry record does not supply enough detail about event definitions, exposure duration or statistical comparisons to support broader conclusions.

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

The primary outcome describes average change in clinic trough FEV1 over Treatment Phase A. The sponsor's dose-response model reports a positive mean difference for FF/UMEC compared with FF, with a 95% confidence interval that excludes zero, and a separate FF/VI estimate with an interval that includes zero. These are findings from the stated analyses in this trial, not a general guarantee about responses in other populations or settings.

Statistical evidence and clinical importance are not interchangeable. A confidence interval and p-value characterize uncertainty under an analysis; they do not say whether the estimated change is large enough to matter to participants. The registry record does not report a threshold for clinical importance for the FEV1 change or the secondary measures. It also does not provide the model details needed to independently reconstruct the sponsor's primary analysis.

The primary results should be interpreted in light of the randomized, double-masked, parallel design, the phase-specific treatment structure and the analysis population stated in the registry. The primary analysis includes randomized participants who received at least one dose, with only those available at the specified time point analyzed. Missing-data methods and multiplicity handling are not reported in sufficient detail.

The secondary outcomes show a generally favorable direction for several FF/UMEC comparisons, but these are multiple outcomes and analyses, with unreported multiplicity handling. They can add descriptive context without serving as independent proof of the primary finding. Safety summaries are also descriptive and have unequal group sizes across phases.

Accordingly, the results do not by themselves establish a treatment recommendation, clinical benefit or comparative safety. They describe the registry's reported statistical estimates and their precision within this study. The recalculated unadjusted contrasts are supplemental checks; because the record flags a discrepancy, the sponsor's own primary analysis takes precedence.

18. Why This Trial Matters Statistically

This trial presents a useful example of why the analysis method matters when interpreting multi-arm dose studies. The arm-level means are distinct, but the sponsor's reported dose-response analysis gives the same mean difference and interval for each listed FF/UMEC comparison. A dose-response model and a set of unadjusted pairwise contrasts answer related but nonidentical statistical questions. Recognizing that distinction prevents readers from treating recalculations as if they reproduce the sponsor's model.

The study also illustrates how precision depends on both the estimated difference and the variability and size of each group. Confidence intervals make uncertainty visible, whereas a single estimate or p-value cannot convey the full range of compatible values. The sponsor's FF/VI interval includes zero, while the FF/UMEC model interval does not; this is a statistical distinction under the reported model, not a clinical judgment.

Finally, multiple doses, endpoints and treatment phases create important interpretation issues. Multiplicity handling, detailed missing-data methods and the original sample-size rationale are not reported. Secondary outcomes and safety counts can help describe the record, but they require caution where group sizes differ and analyses are not fully specified. These features make the registry record a practical case for separating what was measured, what was modeled, and what remains uncertain.

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.

The registry record leaves several trial-specific limitations. It does not report the original sample-size justification, the full statistical analysis plan, detailed model specifications for the primary dose-response analysis, or the multiplicity strategy. The same sponsor estimate is listed for each FF/UMEC dose comparison, but the record does not explain the model output or selection procedure sufficiently to clarify that repetition.

The primary analysis population is defined as randomized participants who received at least one dose, and only participants available at the specified time point were analyzed. The record does not describe the amount or pattern of missing data, the method used to handle missing observations, or sensitivity analyses. Consequently, the effect of missingness on the estimates cannot be assessed from the registry record.

The trial included several treatment arms and staged treatment phases, and safety group sizes differ from the primary endpoint group sizes. This makes it important not to assume that every reported count represents the same analysis population or exposure period. The registry summaries do not provide detailed exposure-adjusted safety comparisons.

The primary results also have a flagged discrepancy between sponsor analyses and simple unadjusted recalculations. The recalculations are based on posted summary statistics and cannot reproduce the sponsor model. The sponsor's own analysis takes precedence, but the lack of model details limits independent verification. Finally, the record does not report a clinical-importance threshold for the primary or secondary outcomes, so statistical differences cannot be translated into clinical importance from these data alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of Umeclidinium Bromide in Combination With Fluticasone Furoate in COPD Subjects With an Asthmatic Component — NCT02164539.
• Registry record last updated 2017-10-11; status last verified 2017-10.
• Results first posted 2016-06-28.
• 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

NCT02164539 is a completed phase 2 randomized, double-masked, parallel-group study sponsored by GlaxoSmithKline, with 338 participants enrolled. It evaluated FF/UMEC dose combinations in COPD participants with an asthmatic component, using change from baseline in clinic trough FEV1 at the end of Treatment Phase A as the primary endpoint.

The sponsor's reported dose-response model gives a mean difference of 0.103 liters for the listed FF/UMEC comparisons with FF, with a 95% confidence interval from 0.014 to 0.193 and p = 0.024. The FF/VI model estimate is 0.073 liters, with a 95% confidence interval from -0.027 to 0.172 and p = 0.152. The registry flags a discrepancy between sponsor analyses and simple unadjusted recalculations, so the sponsor analysis takes precedence.

Several secondary outcomes and descriptive safety results are also recorded. Multiplicity handling, detailed missing-data methods, the original sample-size rationale and full model specifications are not reported in the registry record.