A Randomized, Double Blind, Placebo Controlled, Incomplete Block, Crossover, Dose Ranging Study to Evaluate the Dose Response of GSK573719 Administered Once or Twice Daily Over 7 Days in Patients With Chronic Obstructive Pulmonary Disease (COPD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Randomized, Double Blind, Placebo Controlled, Incomplete Block, Crossover, Dose Ranging Study to Evaluate the Dose Response of GSK573719 Administered Once or Twice Daily Over 7 Days in Patients With Chronic Obstructive Pulmonary Disease (COPD) (NCT01372410), a randomized phase 2 study. The primary outcome is Change From Baseline in Trough Forced Expiratory Volume in One Second (FEV1) on Day 8 of Each Treatment Period.

2. Clinical Question

The design is a randomized, double-blind, placebo-controlled, incomplete-block crossover study. Each participant could contribute measurements under treatment periods, but the registry record does not describe which treatment sequences individual participants received. The incomplete-block structure means the posted results should be read as treatment-group estimates from the study design, not as evidence that every participant received every listed treatment.

The study was registered as Phase 2 and enrolled 163 participants. The registry record lists the study as completed. The primary endpoint compares each treatment-period change with that period’s baseline, with placebo serving as the main reference for the posted treatment contrasts. The central statistical question is therefore the size and precision of the estimated between-treatment differences, rather than whether a single within-group change is positive or negative.

3. Trial Design

This was a randomized, double-blind, placebo-controlled crossover dose-ranging study in participants with COPD. The registry record identifies the model as crossover and the allocation as randomized. It also describes the design as an incomplete block. Double blinding is recorded, but the registry record does not report who was blinded or how the blinding was maintained. It does not report the treatment sequence, period washout arrangements, or the rationale for the incomplete-block allocation.

GSK573719 was evaluated at four once-daily dose levels and two twice-daily dose levels. The treatment periods lasted 7 days. The study also included placebo and tiotropium 18 µg once daily as an active control. The registry description says tiotropium was delivered via the Handihaler. No further device or administration details for the GSK573719 groups are reported in the registry record.

The primary outcome was change from baseline in trough FEV1 on Day 8 of each treatment period. The endpoint timeframe is baseline and Day 8 of each treatment period, up to Study Day 50. The primary analysis used the mITT population, defined in the registry record as participants with at least one post-baseline assessment and non-missing covariate data; reported participant counts reflect those who provided data at Day 8. The registry record lists additional outcomes involving serial FEV1 and weighted mean FEV1 over 0 to 24 hours after morning dosing on Day 7.

Enrollment was 163. The recorded study start was 2011-07-01, and primary completion was 2011-10-01. These dates describe the registry record and do not establish the timing of every treatment period or analysis. The registry record does not report the original sample-size justification, the planned allocation across sequences, an interim-analysis plan, or a detailed missing-data strategy. Those omissions limit reconstruction of the intended design and its prespecified operating characteristics.

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 were randomized to receive a sequence of 3 of 8 possible treatments over 3 treatment periods. There are 56 combinations of 3 treatments from the 8 study treatments, each of which can be ordered in 6 ways (totaling 336 possible sequences; 163 were randomly assigned). Participant Flow data are presented by treatment rather than sequence.

Only the first 6 of 8 groups are shown.

Treatment Period 1 (7 Days)

Reasons for not completing this period:

Washout Period 1 (10-14 Days)

Reasons for not completing this period:

Treatment Period 2 (7 Days)

Washout Period 2 (10-14 Days)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: mITT Population: par. randomized to treatment who received \>=1 dose of study medication. Par. with \>=1 post-BL assessment and non-missing covariate data are included in the analysis. Different par. may have been analyzed at different time points (n=X in category titles); the overall number of par. analyzed reflects everyone in the mITT Population.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Trough Forced Expiratory Volume in One Second (FEV1) on Day 8 of Each Treatment Period, measured over Baseline and Day 8 of each treatment period (up to Study Day 50).

The primary endpoint was change from baseline in trough forced expiratory volume in one second (FEV1), measured in liters, on Day 8 of each treatment period. FEV1 is defined in the registry record as the maximal amount of air that can be forcefully exhaled in one second. Trough FEV1 on Treatment Day 8 is the value measured 24 hours after the morning dose administered on Day 7. For each period, change was calculated relative to the FEV1 value recorded before dosing on Day 1 of that period.

FEV1 is used as a physiological measure of airflow and provides a continuous outcome. A continuous measurement preserves information about the magnitude of change rather than reducing results to whether participants crossed a threshold. For this trial, the statistical focus is on estimated mean change and the contrast between each active treatment and placebo. The outcome is an indicator of lung function under the study conditions; it does not, on its own, capture how participants felt or functioned, nor does it establish effects beyond the short treatment periods studied.

The registry describes the arm summaries as least-squares means with standard errors. The mixed model included mean baseline, period baseline, treatment, and period as fixed effects, and participant as a random effect. Accounting for baseline and period is relevant to a crossover analysis because the outcome is measured repeatedly across treatment periods and baseline values can vary. The reported estimates are model-based summaries, rather than simple raw averages of all measurements.

The primary endpoint was assessed in the mITT population. The registry record specifies that participants needed at least one post-baseline assessment and non-missing covariate data, and that the stated counts correspond to Day 8 data. It does not report the missing-data assumptions used in fitting the model or sensitivity analyses for missing observations.

7. Results Posted in the Registry

• UMEC 15.6 µg QD: mean 0.04 versus -0.07 on control; difference 0.11 (95% CI 0.05 to 0.17), standardized effect d = 0.67; z-test p = <0.001.
• UMEC 31.25 µg QD: mean 0.03 versus -0.07 on control; difference 0.10 (95% CI 0.04 to 0.16), standardized effect d = 0.59; z-test p = 0.002.
• UMEC 62.5 µg QD: mean 0.05 versus -0.07 on control; difference 0.12 (95% CI 0.06 to 0.18), standardized effect d = 0.73; z-test p = <0.001.
• UMEC 125 µg QD: mean 0.11 versus -0.07 on control; difference 0.18 (95% CI 0.12 to 0.24), standardized effect d = 1.08; 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.

Change From Baseline (BL) in Weighted Mean FEV1 Over 0 to 24 Hours After the Morning Dosing on Day 7 of Each Treatment Period

• 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:
  • UMEC 15.6 µg QD: mean 0.04 versus -0.07 on control; difference 0.12 (95% CI 0.07 to 0.17), standardized effect d = 0.88; z-test p = <0.001.
  • UMEC 31.25 µg QD: mean 0.04 versus -0.07 on control; difference 0.12 (95% CI 0.07 to 0.17), standardized effect d = 0.89; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for UMEC 15.6 µg QD 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 UMEC 31.25 µg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes involving serial FEV1 over time on Day 7 and weighted mean FEV1 over 0 to 24 hours after morning dosing on Day 7. The posted weighted-mean summaries show positive estimated changes in the active-treatment groups and a negative placebo estimate. The recalculated placebo contrasts available for the first two once-daily dose groups are positive, with unadjusted p-values <0.001. These results broadly follow the direction of the primary endpoint, which compares trough FEV1 after the treatment period rather than weighted mean FEV1 across the dosing interval.

The secondary measures are related to the primary result because they assess FEV1, but they represent different features and measurement times. A weighted mean across 0 to 24 hours reflects lung-function measurements across a dosing interval, while the primary endpoint is a trough measurement 24 hours after the Day 7 morning dose. Serial FEV1 over time provides a time profile. Agreement in broad direction across related measures can add context, but the endpoints are not interchangeable and do not answer exactly the same question.

The registry record lists six outcome measures and nine analyses, but the secondary outcome information does not provide a complete set of sponsor-reported inferential comparisons for every listed endpoint. Detailed secondary analyses, confidence intervals, and p-values are not reported in the registry record for the weighted-mean outcome as sponsor analyses. The posted summary values and recalculations should therefore be interpreted with the stated limitations, rather than as a complete confirmatory analysis.

Secondary findings generally carry less inferential weight when multiple endpoints and comparisons are examined without a reported multiplicity plan. Each additional test creates more opportunity for a nominally unusual result, and correlated outcomes do not remove that issue. The registry record does not report whether secondary outcomes were prespecified as confirmatory, whether tests were ordered in a hierarchy, or whether p-values were adjusted. The primary endpoint remains the clearest stated basis for the main treatment comparison; secondary results offer supporting descriptive context, not independent confirmation by default.

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

• Change From Baseline (BL) in Serial FEV1 Over Time on Day 7 of Each Treatment Period
• Change From Baseline (BL) in Weighted Mean FEV1 Over 0 to 24 Hours After the Morning Dosing on Day 7 of Each Treatment Period

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mixed model represent?

The registry reports a mixed-model analysis for the primary endpoint. In general, a mixed model can represent both fixed effects, which describe systematic contrasts of interest, and random effects, which account for clustering or repeated measurements. Here, treatment and period were fixed effects, and participant was a random effect. The model also included mean baseline and period baseline. This structure recognizes that the study collected measurements across treatment periods and that measurements from the same participant are not necessarily independent.

The primary endpoint is a change from baseline, but the model description includes baseline terms as covariates. Mean baseline is the mean of a participant’s baseline measurements across periods. Period baseline is defined in the record as the difference between that period’s baseline and the participant’s mean baseline. Together with the period term, these covariates allow the model to account for baseline level and differences between treatment periods when estimating treatment contrasts. The registry record does not provide the model formula, covariance structure, or diagnostics.

What is a least-squares mean?

A least-squares mean is a model-based estimate of a group mean after accounting for variables included in the analysis. It is not necessarily identical to the unadjusted arithmetic average of observed values. In this trial, the posted arm values are least-squares mean changes, and the reported dispersion is a standard error. The standard error describes the estimated uncertainty of the mean estimate; it is not a measure of the spread of individual participant outcomes.

Because the estimates are model-based, the comparison of treatments should be interpreted through the model’s estimated contrasts and their confidence intervals. The registry’s reported analyses give mean differences, 95% confidence intervals, and p-values for comparisons with placebo. The unadjusted recalculations use posted summary statistics and are not a replacement for the sponsor’s mixed-model analysis. Where the two presentations are not identical, the sponsor’s own analysis takes precedence; the registry record does not flag a discrepancy.

Why does crossover structure matter?

In a crossover study, participants contribute measurements under treatment periods, so their observations can be related. A model that includes participant as a random effect can account for this repeated-measures structure. Period terms can address systematic differences associated with the treatment period itself. In general, crossover interpretation also depends on assumptions about period effects, carryover, and treatment sequence. The registry record does not report whether carryover was assessed, what washout arrangements were used, or how sequences were incorporated into the model. Those features should not be inferred from the word “crossover” alone.

The incomplete-block designation means the registry does not describe a design in which every participant necessarily received every listed treatment. The treatment-specific counts also vary. It is therefore important not to treat the arm-level summaries as if each comparison were a conventional parallel-group trial with independent, unrelated participants. The reported mixed model is the stated analysis framework; more detailed information about its implementation is not reported in the registry record.

How should the p-values be read?

A p-value describes how compatible the observed data are with a specified statistical null model, under the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not quantify the size or clinical importance of an effect. The sponsor-reported p-values for each primary comparison with placebo were <0.001. This indicates that the model-based data were inconsistent with a zero mean difference under the stated test, but it does not settle the questions of clinical importance, durability, or generalizability.

The registry record reports multiple dose and frequency comparisons with placebo. It does not report whether or how the primary comparisons were adjusted for multiplicity. When many comparisons are examined, the chance of at least one apparently unusual result can increase; general methods for addressing this include prespecifying a hierarchy or adjusting inference across comparisons. Without a reported plan, the listed p-values should be read as the reported comparisons, not assumed to have a particular family-wise error control.

What do the recalculations add?

Recalculated comparisons use the posted arm means and standard errors to produce simple, unadjusted estimates and intervals. Their pooled standard deviations are approximate because the arm summaries report standard errors rather than individual-level variability. The calculations are useful as a transparent check on the scale and direction of the contrasts, but they do not reproduce all features of the sponsor’s mixed model. They cannot account independently for the crossover correlation, the specified baseline adjustments, or any unreported model details.

The recalculated p-values are also unadjusted comparisons, so they should not be treated as the trial’s definitive inferential analysis. The reported sponsor analyses directly state the mixed-model mean differences and confidence intervals. Since the record does not identify a discrepancy, the recalculations can be read as broadly consistent checks, while the sponsor estimates remain the primary basis for describing the registry analysis.

What remains unknown about the analysis?

The registry record does not report a statistical analysis plan, the prespecified multiplicity strategy, the original sample-size justification, or interim analyses. It does not describe the missing-data assumptions, sensitivity analyses, model diagnostics, or the handling of possible carryover. These are not details that can be reconstructed from the summary estimates. Their absence matters because they affect how fully an independent reader can assess model robustness and the planned interpretation of multiple treatment contrasts.

11. Confidence Intervals and Precision

A confidence interval describes a range of values reasonably compatible with the data and the statistical model, rather than a guaranteed range containing the true effect. The sponsor-reported primary comparisons are presented with 95% confidence intervals. For UMEC 125 µg QD versus placebo, the estimated mean difference was 0.183 liters, with an interval from 0.127 to 0.239. For the other listed primary contrasts, the lower and upper bounds were also positive. The intervals therefore indicate uncertainty around positive model-based mean differences relative to placebo, while not eliminating uncertainty about their exact size.

Interval width reflects both the precision of the estimate and the information available under the analysis. Narrower intervals indicate greater precision for the corresponding contrast, all else equal. The registered primary arm standard errors are 0.022 or 0.023 liters, and the sponsor-reported intervals differ in width across contrasts. Those summaries do not reveal the full distribution of participant outcomes or the degree of overlap between individuals in the treatment groups.

The recalculated intervals are based on rounded arm-level means and standard errors, with an approximate pooled standard deviation. They are simple, unadjusted comparisons and are not the same as intervals from the full mixed model. For inference, the sponsor’s mixed-model results are the relevant registry analyses. A confidence interval for a mean difference also should not be confused with an interval for an individual participant’s outcome or a prediction interval.

Precision is specific to the endpoint, timing, model, and analysis population. The primary results concern trough FEV1 on Day 8 after treatment over 7 days in each period. They do not directly quantify precision for long-term outcomes or other clinical measures. The registry record does not report prespecified thresholds for clinical importance, so the intervals alone cannot establish whether the estimated differences are meaningful to patients.

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 participants per arm, not total event counts. They are illustrative calculations based on the observed effect, using a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each scenario asks how many participants per arm would be needed to detect the stated fraction of the observed effect. These are planning illustrations, not observed power.

The 80% power column gives the estimated participants per arm under the stated assumptions for an 80% chance of detecting the selected effect if that effect were the true one. The 90% power column uses a higher target chance of detection under the same general setup. These are design calculations, not probabilities that the observed finding is correct. They also do not show the power of the completed crossover study; the calculations are framed as two-arm planning illustrations and do not reproduce its full design or mixed-model analysis.

For each comparison, the full observed effect is one planning scenario. The other scenarios plan for 75% and 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same assumptions. This is why the participant estimates rise as the target effect is reduced. The values are sensitive to the observed effect used as the starting point, which can itself be uncertain. They should not be read as the original trial’s sample-size rationale: that rationale and the study’s own original design assumptions are not reported in the registry record.

The listed values also do not account for all features of the actual incomplete-block crossover design, because the calculation assumes equal allocation between two arms. They are most useful as a general illustration of how the assumed effect size and desired power affect planning, rather than as a direct recommendation for a future study.

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 = 0.112; pooled standard deviation σ = 0.168.
2. n = 2 × (1.96 + 0.842)² × 0.168² / 0.112² = 35.4, rounded up to 36 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 <- 0.112                      # observed difference in means
sigma <- 0.168273896810605                     # 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(1372410)
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 = 36 (80% power), 48 (90% power)
 75% of observed effect: n per arm = 63 (80% power), 85 (90% power)
 50% of observed effect: n per arm = 142 (80% power), 190 (90% power)
power.t.test: 36.4 
Simulated power at n = 36 per arm: 0.790 (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 analyses use mixed models and compare each active-treatment group with placebo. For example, the reported mean difference for UMEC 125 µg QD was 0.183 liters, with a 95% confidence interval from 0.127 to 0.239 and p <0.001. The sponsor also reported positive mean differences for the other listed GSK573719 regimens and for tiotropium, each with p <0.001.

The recalculated contrasts are simple, unadjusted checks based on the posted arm means and standard errors. They do not reproduce the full crossover model or its baseline and period adjustments, and the pooled variability used in the recalculation is approximate. Consequently, their values may not match the sponsor’s model-based estimates exactly. The registry record does not flag a discrepancy, but the sponsor’s own analysis remains the appropriate source for the trial’s reported inferential results.

Both approaches point to positive estimated differences from placebo, but their estimates should not be conflated. The sponsor’s confidence intervals and p-values arise from the reported mixed-model analyses. The recalculated results serve as supplementary checks of the posted summaries; they are not an independent reanalysis of participant-level data and do not address unreported analytic choices.

The sponsor analyses listed are comparisons against placebo. They do not report direct statistical comparisons among the GSK573719 doses or between GSK573719 and tiotropium. The relative size of separate estimates is not a substitute for those direct tests.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint has multiple treatment comparisons with placebo across several once-daily and twice-daily GSK573719 regimens, as well as the tiotropium active control. When a study makes multiple statistical comparisons, the chance of at least one false-positive finding can be higher than for a single prespecified comparison. General approaches include adjusting significance thresholds, controlling a family-wise error rate, or specifying an ordered testing strategy. The registry record does not report which, if any, approach was used. The listed sponsor p-values should therefore be read as reported, without assuming a particular multiplicity adjustment.

The record gives the primary model structure and defines the mITT population as participants with at least one post-baseline assessment and non-missing covariate data. It further states that the primary outcome counts represent participants who provided data at Day 8. This identifies an analysis population rule, but it does not describe how missing observations were handled within the model, whether imputation was used, or whether results were tested under alternative assumptions. Those details are not reported in the registry record.

The registry does not report an analysis plan, interim-analysis details, the sample-size justification, model diagnostics, or sensitivity analyses. It also does not describe a prespecified hierarchy for primary and secondary endpoints. Without those details, it is not possible to determine from the record whether the posted analyses follow a fully specified plan or how robustness to alternative analytic choices was assessed. This is a limit on the completeness of statistical interpretation, not evidence that a particular method was or was not used.

For a crossover study, period and participant effects matter, and the stated mixed model includes period as a fixed effect and participant as a random effect. The registry record does not report details about treatment sequence, washout, carryover assessment, or the covariance structure. These omissions leave important aspects of the model’s assumptions and implementation unclear. They also limit the ability to reproduce the analysis from the posted summary statistics alone.

Related endpoints and multiple dose regimens can make a coherent pattern informative, but they do not remove multiplicity concerns. The secondary findings should not be treated as additional confirmatory evidence unless the analysis plan and adjustment strategy support that interpretation; those plans are not reported in the registry record.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: myocardial infarction (1.8%), acute respiratory failure (1.7%).

The serious adverse event summaries report the number of participants at risk and the number affected in each listed treatment group. The registry reports one serious adverse event in the UMEC 15.6 µg QD group and one in the UMEC 31.25 µg QD group; no serious adverse events were listed for the other treatment groups. These are group-specific registry counts and should not be added together to infer a count of distinct participants, particularly given the crossover design.

For other adverse events, the posted counts range from none to eight affected participants across the groups. The largest listed count is eight in the UMEC 125 µg QD group. These summaries are descriptive and do not by themselves establish comparative risk. The record also lists myocardial infarction at 1.8% and acute respiratory failure at 1.7% among top serious-event terms, without further group-specific detail in that listing.

Deaths are not reported in the registry record. The adverse-event summaries cover the study record and short treatment periods; they do not establish long-term safety. Group counts should be interpreted alongside the study design and duration, and not as a complete assessment of uncommon or delayed events.

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

The posted primary results show positive model-based mean differences in trough FEV1 for each listed active-treatment group compared with placebo at the measured time point. The largest estimated difference was for UMEC 125 µg QD, while the other GSK573719 regimens and tiotropium also had positive sponsor-reported comparisons. The 95% confidence intervals and p-values describe statistical uncertainty under the reported model; they do not make the estimates exact or remove uncertainty about clinical relevance.

The endpoint is a short-term physiological measure. It captures forced expiratory volume in one second at trough after treatment over 7 days in each period. It does not directly measure symptoms, quality of life, exacerbations, hospitalization, or survival. Those outcomes are not reported as the focus of the primary result. The posted FEV1 findings therefore should not be used as a substitute for evidence on those other outcomes.

The study’s dose-ranging structure allows observation of estimated changes across multiple doses and dosing frequencies, but the registry comparisons are each against placebo. They do not establish that one dose is superior to another, that once-daily and twice-daily regimens differ, or that tiotropium and a GSK573719 regimen are equivalent. Those conclusions require direct contrasts and appropriate uncertainty estimates, which are not reported in the registry record.

Statistical evidence of a nonzero average difference is not the same as proof that the effect is clinically important for every participant. Group means can conceal variation in individual responses, and standard errors describe precision of estimated means rather than the range of individual outcomes. The registry record does not provide a threshold for clinical importance, so the size of the difference cannot be classified against such a threshold from these results alone.

The record also does not establish whether the observed short-term pattern persists over longer treatment or applies outside the studied COPD population. Interpretation is limited to the population, endpoint, treatment periods, and model reflected in the registry. The primary findings are best understood as estimates of mean trough FEV1 change under the trial conditions, with uncertainty and design limitations kept in view.

18. Why This Trial Matters Statistically

Statistically, this study is informative because it evaluates several dose levels and dosing frequencies within a randomized, double-blind, placebo-controlled crossover framework. That design can provide treatment-period comparisons while accounting for repeated observations within participants. The posted analysis reflects this structure by including participant as a random effect and treatment and period as fixed effects. These features make the model-based estimates more relevant than an unadjusted comparison that ignores the design.

The record also illustrates why the endpoint and its timing matter. Trough FEV1 at Day 8 is not the same measure as a weighted mean across a dosing interval or a serial time profile. Considering related FEV1 outcomes can help describe whether the pattern is consistent across measurement definitions, but those outcomes remain distinct and their analyses require appropriate attention to multiplicity.

The dose-ranging results show a range of estimated placebo contrasts, rather than a uniform increase at every successive dose. This makes it important to avoid treating the study as a simple linear dose-response test or inferring direct differences from the ordering of point estimates. Dose-specific estimates are descriptive unless supported by a suitable direct comparison or a prespecified dose-response model; neither such a comparison nor model is reported in the registry record.

The study is also a useful reminder that precision and design are inseparable. The reported standard errors and confidence intervals concern model-based mean changes, while the crossover and incomplete-block features affect how observations relate across treatments. Summary statistics alone cannot fully reconstruct that model. The sponsor’s mixed-model analyses are therefore central, with recalculations serving only as approximate checks.

Finally, the record’s omissions about multiplicity, missing-data handling, and the original planning assumptions are statistically consequential. They do not negate the reported estimates, but they constrain how strongly the findings can be generalized or treated as confirmatory. Clear distinction between model-based results, unadjusted checks, secondary outcomes, and planning illustrations is essential for sound interpretation.

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 trial focused on treatment periods of 7 days, with the primary outcome assessed at trough on Day 8. This duration and endpoint do not support conclusions about longer-term persistence of FEV1 changes or outcomes over extended treatment. The registry record does not report longer-term follow-up results.

The design is described as an incomplete-block crossover, but the record does not report treatment sequences, washout arrangements, or carryover assessment. These details are relevant to judging whether effects from an earlier period could influence later measurements. The mixed model included period and participant effects, but the record does not provide enough implementation detail to assess the full handling of sequence and within-participant correlation.

The primary analysis population has a stated definition, but the registry does not describe the extent or pattern of missing observations, missing-data assumptions, imputation, or sensitivity analyses. Day 8 counts vary across treatment groups, and the record says these counts refer to participants who provided data at Day 8. Without further information, the impact of incomplete observations on estimates cannot be fully evaluated.

Several dose and frequency comparisons were made against placebo, and related secondary outcomes were also listed. The multiplicity strategy is not reported. Direct comparisons among active treatments are not included in the posted primary analyses, so relative dose or schedule claims cannot be established from separate placebo contrasts.

Lastly, the registry record does not report the original sample-size rationale, interim analyses, or a complete statistical analysis plan. The planning illustrations based on observed effects are not a substitute for the trial’s original design assumptions. These limitations qualify the strength and scope of interpretation, without changing the direction of the posted primary estimates.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Randomized, Double Blind, Placebo Controlled, Incomplete Block, Crossover, Dose Ranging Study to Evaluate the Dose Response of GSK573719 Administered Once or Twice Daily Over 7 Days in Patients With Chronic Obstructive Pulmonary Disease (COPD) — NCT01372410.
• Registry record last updated 2017-11-08; status last verified 2017-10.
• Results first posted 2014-02-11.
• 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 describes a completed Phase 2, randomized, double-blind, placebo-controlled incomplete-block crossover study of GSK573719 in COPD. Enrollment was 163. Treatment groups included once-daily and twice-daily GSK573719 regimens, placebo, and tiotropium 18 µg once daily.

The primary endpoint was change from baseline in trough FEV1 on Day 8 of each treatment period. Sponsor-reported mixed-model comparisons with placebo were positive for each active-treatment group, with 95% confidence intervals and reported p-values. The largest estimate was for UMEC 125 µg QD. The registry also lists serial and weighted mean FEV1 secondary outcomes and adverse-event summaries.

Interpretation is limited by unreported details about multiplicity, missing-data handling, treatment sequences, carryover, and original sample-size planning. The posted results describe short-term mean FEV1 changes under the study conditions and do not establish direct differences among active regimens or longer-term clinical outcomes.