GSK573719 Dose Ranging Study in Chronic Obstructive Pulmonary Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for GSK573719 Dose Ranging Study in Chronic Obstructive Pulmonary Disease (NCT00950807), a randomized phase 2 study. The primary outcome is Change From Baseline in Trough Forced Expiratory Volume in One Second (FEV1) at Day 15 of Each Treatment Period.

2. Clinical Question

The endpoint is a lung-function measure recorded repeatedly over treatment periods. The crossover design means treatment comparisons were evaluated within a study in which participants could receive different treatments in different periods; however, the treatment sequence and period-specific participation are not fully described in the registry record. The central statistical question is therefore about the estimated difference in mean change under each regimen relative to placebo, while taking account of the repeated-period design described for the primary analysis. The results are estimates of this endpoint in the analyzed population, not a complete account of every possible clinical outcome.

3. Trial Design

This was a randomized, quadruple-masked, phase 2, placebo-controlled crossover study in participants with COPD. The registry lists an enrollment of 176 and a completed study. The listed study dates are 2009-09-01 for study start and 2010-03-01 for primary completion. These dates describe the registry record and do not by themselves provide information about the timing or conduct of individual treatment periods.

The treatment set included placebo, tiotropium, and multiple GSK573719 regimens. The once-daily doses listed were 62.5, 125, 250, 500, and 1000 µg; twice-daily doses were 62.5, 125, and 250 µg. The primary endpoint was collected at Day 15 of each treatment period, with the timeframe extending up to Study Day 71. Secondary outcomes concerned weighted mean FEV1 over 0 to 24 hours after dosing on Day 14 and serial FEV1 over 0-28 hours after the morning dose on Day 14.

Randomization helps guard against systematic allocation differences, while masking is intended to limit influences from treatment knowledge on participant experience and outcome assessment. In a crossover design, the same participant may contribute observations under more than one treatment, so statistical analysis must account for the structure of measurements across periods. The registry describes a mixed model for the primary endpoint, including participant as a random effect and treatment and period among the fixed effects. It does not report the randomization sequence, washout duration, treatment-period duration beyond the endpoint timing, or rules for changing or discontinuing treatment. Those features should not be inferred from the design label alone.

The registry describes the study as evaluating safety, efficacy, dose response, and pharmacokinetics. The detailed posted results considered in this statistical interpretation are centered on FEV1. The record does not provide enough information to reconstruct all operational details of the crossover or the full study protocol.

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 (par.) who were eligible completed a 4- to 7-day Run-in period prior to randomization. The treatment (trt) phase was comprised of three 14-day trt periods. Par. were randomly assigned to receive a sequence of placebo and 2 of the 9 active trts over the trt phase. Participant Flow data are presented by treatment rather than sequence.

Only the first 6 of 10 groups are shown.

Treatment Period 1

Reasons for not completing this period:

Washout Period 1

Reasons for not completing this period:

Treatment Period 2

Reasons for not completing this period:

Washout Period 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified Intent-To-Treat (mITT) Population: all participants randomized to treatment who received at least one dose of study medication. All participants with \>=1 post-baseline assessment and non-missing covariate data are included in the analysis. The number of participants represents participants who provided data at Day 15.

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) at Day 15 of Each Treatment Period, measured over Baseline and Day 15 of each treatment period (up to Study Day 71).

The primary endpoint is change from baseline in trough forced expiratory volume in one second (FEV1), measured at Day 15 of each treatment period and expressed in liters. FEV1 is the maximal amount of air that can be forcefully exhaled in one second. The registry defines the trough value as the measurement taken 24 hours after the morning dose on Day 14. Change for a treatment period is the Day 15 trough value minus that period’s baseline value, recorded before dosing on Day 1.

FEV1 is used as a continuous measure of lung function. In general, continuous outcomes retain information about the magnitude of measurements rather than reducing them to a yes-or-no category. The primary result is expressed as a least-squares mean change for each treatment, alongside a standard error. A least-squares mean is a model-based estimate that accounts for the covariates and design terms included in the analysis; it is not necessarily the simple arithmetic average of the observed measurements.

The endpoint is measured separately within treatment periods, which aligns with the crossover design and allows the model to include period and participant effects. The outcome therefore addresses the average measured change in FEV1 at a specified trough time, not every aspect of lung function, symptoms, daily functioning, or longer-term outcomes. The registry’s endpoint description identifies the measure and timing, but does not establish how a particular change should be interpreted as important to an individual participant.

7. Results Posted in the Registry

• UMEC 62.5 µg QD: mean 0.08 versus -0.05 on control; difference 0.13 (95% CI 0.06 to 0.20), standardized effect d = 0.62; z-test p = <0.001.
• UMEC 125 µg QD: mean 0.10 versus -0.05 on control; difference 0.15 (95% CI 0.07 to 0.22), standardized effect d = 0.71; z-test p = <0.001.
• UMEC 250 µg QD: mean 0.05 versus -0.05 on control; difference 0.10 (95% CI 0.02 to 0.17), standardized effect d = 0.46; z-test p = 0.010.
• UMEC 500 µg QD: mean 0.09 versus -0.05 on control; difference 0.14 (95% CI 0.07 to 0.21), standardized effect d = 0.68; 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 Obtained Post-dose on Day 14 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 62.5 µg QD: mean 0.09 versus -0.06 on control; difference 0.14 (95% CI 0.09 to 0.20), standardized effect d = 0.88; z-test p = <0.001.
  • UMEC 125 µg QD: mean 0.08 versus -0.06 on control; difference 0.14 (95% CI 0.08 to 0.19), standardized effect d = 0.83; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for UMEC 62.5 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 125 µg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry identifies two secondary FEV1 outcomes: weighted mean FEV1 over 0 to 24 hours after dosing on Day 14, and serial FEV1 over 0-28 hours after the morning dose on Day 14. The posted arm summaries for the weighted-mean outcome show a negative placebo mean change and positive mean changes for the active treatment labels. The reported values are model-based least-squares means with standard errors. Those summaries are directionally consistent with the primary endpoint’s broad pattern of positive active-treatment estimates and a negative placebo estimate.

The registry record does not include posted numerical arm results or treatment contrasts for the serial FEV1 outcome. Its title and measurement window identify what was assessed, but do not establish the direction, size, or precision of any treatment differences for that outcome. It is therefore not possible to claim that both secondary outcomes independently corroborate the primary result. Detailed statistical comparisons for the weighted-mean outcome are also not available in the reported-analysis list.

Secondary outcomes can help describe whether the primary endpoint’s pattern appears across related measurements and time windows. They do not automatically provide independent confirmation: the outcomes may be correlated because they measure FEV1 in the same study and participants. In addition, interpreting several outcomes and treatment comparisons creates a multiplicity issue. When many hypotheses are assessed, the chance of at least one apparently unusual result can increase unless the analysis plan accounts for that testing structure.

The registry record does not report whether secondary outcomes were designated as confirmatory, how their testing was ordered, or whether any multiplicity adjustment was applied. Consequently, secondary findings should carry less inferential weight than the prespecified primary result, and unreported outcome details should not be filled in by assumption. The secondary information offers context about the outcome program, but it cannot be treated as a complete independent test of the primary conclusion.

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

• Change From Baseline (BL) in Weighted Mean FEV1 Over 0 to 24 Hours Obtained Post-dose on Day 14 of Each Treatment Period
• Change From Baseline (BL) in Serial FEV1 Over 0-28 Hours After the Morning Dose at Day 14 of Each Treatment Period

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint was analyzed with a mixed model. The registry states that the model included mean baseline, period baseline, treatment, and period as fixed effects, and participant as a random effect. Mean baseline was defined as the mean of a participant’s baseline values across periods; period baseline was the difference between the baseline in a particular treatment period and that participant’s mean baseline. Change from baseline was calculated within each treatment period.

Why use a mixed model?

General explanation: A mixed model can represent both systematic features shared across participants and variation associated with individual participants. Fixed effects estimate average relationships for specified model terms, such as treatment and period. A random participant effect allows observations from the same participant to be related rather than treating them as independent. This is relevant in repeated-measure and crossover settings, where one participant may contribute more than one observation. The model’s validity still depends on appropriate assumptions about the outcome, design, and missingness.

The registry describes least-squares mean changes for each treatment and standard errors. A least-squares mean is adjusted according to the model terms; the standard error describes the estimated sampling variability of that mean. The listed arm counts differ across treatment labels, and the primary analysis population required at least one post-baseline assessment and non-missing covariate data. The registry does not give a full account of how incomplete period sequences or other missing observations were handled.

How do treatment contrasts work?

The registry’s reported comparisons are mixed-model mean differences between placebo and each treatment. A positive difference means the estimated mean change for that treatment is higher than the placebo estimate on the stated scale. The reported 95% confidence intervals give a range of values compatible with the data and model at that confidence level; a narrower interval indicates greater precision than a wider interval. A confidence interval is not a guarantee that the true value lies inside the interval, and it does not describe variation among individual participants.

The registry also reports p-values for those contrasts. A p-value measures how unusual the observed data, or more extreme data, would be under a specified null hypothesis and model. It is not the probability that the null hypothesis is true, nor does it quantify the size or importance of a treatment difference. The reported contrasts use the sponsor’s mixed-model analysis. The record does not say whether multiplicity adjustments were applied to these comparisons.

What does the recalculation add?

The recalculated contrasts are simple, unadjusted calculations from posted arm summaries. The pooled standard deviations used for that exercise are approximations derived from the arm standard errors and sample sizes, rather than the participant-level data or the full crossover model. The recalculation can provide a transparent check on the scale and direction of the contrasts, but it does not reproduce the registry’s mixed model, its covariate structure, or the dependence among observations within participants. Where the two approaches differ, the sponsor’s own analysis takes precedence.

Some recalculated confidence limits contain more decimal places in the underlying calculation than are appropriate for interpretation alongside the rounded registry estimates. The interpretation should focus on the posted precision and avoid implying that a simple unadjusted calculation is more exact than the model-based result. The registry’s reported estimates and intervals are the primary inferential results for these comparisons.

How should power calculations be understood?

General explanation: Power is the probability that a study would reject a specified null hypothesis under a particular alternative effect and set of assumptions. A planning calculation uses assumptions about effect size, variability, significance level, allocation, and analysis. It is not a retrospective measure of whether an observed result was “powered.” The registry record’s planning illustration is based on a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and a target effect set to a stated fraction of the observed effect. These are planning assumptions for the illustration, not documented assumptions used to design the trial.

11. Confidence Intervals and Precision

The registry reports 95% confidence intervals for the primary treatment-versus-placebo mean differences. These intervals express the precision of the estimated average contrast under the sponsor’s mixed-model analysis. For UMEC 1000 µg once daily, the reported mean difference was 0.186 liters, with a 95% confidence interval from 0.113 to 0.259. For UMEC 62.5 µg twice daily, the reported difference was 0.079 liters, with a 95% confidence interval from 0.008 to 0.151. The interval for each reported comparison lies above zero, while the interval widths vary across comparisons.

In general, an interval’s width reflects both the amount of information and the variability represented in the model. Wider intervals indicate less precision about the average contrast; narrower intervals indicate more precision. The arm counts in the primary outcome vary by regimen, and the estimated standard errors also vary. Those features are consistent with differing precision across contrasts, but the registry record does not provide participant-level data for a deeper assessment of why each interval has its particular width.

Confidence intervals should be read together with the point estimate. The point estimate is the model’s best estimate under its assumptions, while the interval shows a range of estimates that remain compatible with the data at the stated confidence level. Neither the point estimate nor its interval describes the full distribution of individual participant changes. The registry does not report a clinical-importance threshold for this endpoint, so the intervals alone cannot establish whether a difference is important in clinical practice.

The simple recalculations use approximate variability from posted summary values and do not reproduce the crossover model. Their intervals are therefore not a substitute for the sponsor’s reported intervals. Because a discrepancy is present, the registry’s own analysis takes precedence. Precision is also conditional on the analysis population and model specification; information about alternative models or sensitivity analyses is not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations give participants per arm for 80% power and participants per arm for 90% power. They do not give total event counts, because these are continuous outcomes rather than time-to-event outcomes. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The trial’s original sample-size assumptions and justification are not reported in the registry record.

The 80% power column means the illustrated number of participants per arm under which the calculation estimates an 80% chance of detecting the target effect, if the assumptions hold. The 90% power column represents a higher chance of detecting that same target effect and generally calls for more participants per arm. For example, planning for 75% of the observed effect for UMEC 125 µg once daily gives 56 participants per arm for 80% power and 75 participants per arm for 90% power. Planning for 50% of that observed effect gives 125 participants per arm for 80% power and 168 participants per arm for 90% power.

Smaller target effects require more participants to distinguish them from random variation under the same assumptions. The rows planning for 100%, 75%, and 50% of the observed effect are alternative planning scenarios, not claims that those effects will occur in a future study. The corresponding curve should be interpreted as a visual expression of the same planning relationship, rather than as an additional result from the trial. These figures are planning illustrations and are not observed power.

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 = 0.128; pooled standard deviation σ = 0.205.
2. n = 2 × (1.96 + 0.842)² × 0.205² / 0.128² = 40.4, rounded up to 41 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 <- 0.128                      # observed difference in means
sigma <- 0.205434516718444                     # 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(950807)
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 = 41 (80% power), 55 (90% power)
 75% of observed effect: n per arm = 72 (80% power), 97 (90% power)
 50% of observed effect: n per arm = 162 (80% power), 217 (90% power)
power.t.test: 41.4 
Simulated power at n = 41 per arm: 0.800 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s own treatment-versus-placebo comparisons using mixed models. Those analyses account for the model terms described for the primary endpoint, including treatment, period, baseline-related covariates, and participant as a random effect. The reported results include a mean difference, a 95% confidence interval, and a p-value for each listed comparison.

The recalculated comparisons are simpler: they use posted arm means and standard errors to form unadjusted contrasts and approximate variability. They do not use participant-level data and do not reproduce the mixed model or the crossover dependence structure. Differences between recalculated and sponsor-reported estimates are therefore possible. For example, the sponsor reports 0.147 liters for UMEC 125 µg once daily versus placebo, while the recalculated estimate is 0.146 liters. The sponsor reports 0.172 liters for UMEC 250 µg twice daily, compared with a recalculated estimate of 0.171 liters.

The recalculation is a check on the broad magnitude and direction of the posted comparisons, not a replacement analysis. Because the registry record indicates a discrepancy, the sponsor’s own analysis takes precedence. Its confidence intervals and p-values should be used when describing the primary inferential results; the recalculated values should be understood as unadjusted illustrations based on summary statistics.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint includes comparisons of several treatment regimens with placebo. The registry record lists nine sponsor-reported comparisons, but does not report whether the p-values or confidence intervals were adjusted for multiple comparisons. When many hypotheses are tested, the chance of at least one result appearing statistically significant by chance can rise. Methods such as a prespecified testing hierarchy or multiplicity adjustment can address this issue, but the analysis plan and any such method are not reported in the registry record. The listed p-values should therefore be read as the reported results, without assuming a family-wise adjustment or an unadjusted testing strategy beyond what is stated.

The record describes the primary analysis population as randomized participants who received at least one dose, with participants included in the analysis if they had at least one post-baseline assessment and non-missing covariate data. This clarifies that the primary analysis was not simply based on every randomized participant regardless of available outcome information. The number of participants contributing to the endpoint differs among treatment labels. The registry does not provide a full participant flow by sequence, the reasons for missing measurements, or a detailed account of how missing observations were handled by the model.

In general, missing-data methods rely on assumptions about why data are missing and how missing observations relate to observed outcomes. A mixed model can use available observations under its modeling assumptions, but the presence of a mixed model alone does not establish that missingness has no effect on the results. The registry does not report sensitivity analyses for alternative missing-data assumptions, imputation procedures, or a comparison of analysis populations.

The crossover structure adds further questions about incomplete periods and participants who may not contribute measurements under every treatment. The stated random participant effect addresses within-participant structure in the model, but the record does not describe all rules for incomplete treatment sequences or carryover assessment. Interim analyses and the statistical plan for the trial are not reported in the registry record. These omissions limit independent assessment of multiplicity, missing-data robustness, and whether all model decisions followed a prespecified plan.

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: chronic obstructive pulmonary disease (2.8%), concussion (2.8%).

The posted safety results list the number of participants at risk and the number affected by serious adverse events and other adverse events for each treatment label. Serious adverse events were reported for 2 participants in the UMEC 250 µg once-daily group and 1 participant in the UMEC 125 µg twice-daily group; the other listed groups show 0 affected participants for this category. The placebo group lists 0 affected participants. These are group-level counts in the registry record and should be read with the corresponding at-risk counts, rather than as rates calculated across the crossover study.

The record lists Chronic obstructive pulmonary disease and Concussion among the top serious adverse-event terms, each with 2.8%. It does not provide enough detail in this summary to establish whether these terms account for all serious events or to describe their timing, severity, or relationship to treatment. Death counts are not reported in the registry record.

Adverse-event counts are descriptive safety information, not a definitive comparison of risk. The treatment groups have different at-risk counts, and participants could experience more than one treatment period in a crossover study. The registry record does not explain how exposure duration or repeated participation was handled in these summaries. These figures should not be used alone to infer comparative safety or to make treatment decisions.

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

The primary results describe average changes in trough FEV1 during the treatment periods represented in the registry record. The sponsor’s mixed-model comparisons report higher mean changes relative to placebo for each listed active regimen, with confidence intervals and p-values that quantify statistical uncertainty under that model. The broad direction of the estimates is consistent across the primary comparisons, but the magnitude varies across regimens and does not form a simple monotonic pattern by dose.

These findings do not establish that every participant experienced an increase, or that an individual participant would have the average change reported for a treatment group. A group mean can conceal substantial variation among participants. Nor does a statistically significant contrast by itself establish that the magnitude is clinically important. The registry record does not state a threshold for a clinically meaningful FEV1 difference.

The result concerns a specific outcome, measurement timing, analysis population, and crossover study. It does not by itself establish effects on symptoms, exacerbations, daily activities, quality of life, long-term outcomes, or other measures not detailed in the posted results. The registry describes safety and pharmacokinetics as study aims, but the available figures summarized for this analysis do not provide a complete account of either domain.

Interpretation also depends on the sponsor’s mixed-model assumptions, handling of incomplete observations, and treatment-period structure. The record gives some model details but not the full protocol or statistical plan. It does not report whether multiplicity adjustments were used across the many treatment comparisons. The reported estimates are useful descriptions of the posted analysis, while uncertainties about these unreported details limit how broadly they can be generalized.

Accordingly, the results should be read as estimates from a completed phase 2 crossover study, not as a universal prediction or a clinical recommendation. They describe the evidence and its precision for the measured endpoint; they do not determine whether a treatment is appropriate for a particular person.

18. Why This Trial Matters Statistically

This trial illustrates several statistical features that are important in clinical research. First, a crossover design produces repeated observations from participants across treatment periods. Analyses need to account for that dependence, and the registry’s mixed model includes a participant random effect as well as period terms. A simple comparison of arm summaries can be informative as a check, but it cannot reproduce the full design-based analysis.

Second, the study evaluates multiple doses and schedules against a placebo comparator, with tiotropium also represented among the treatments. That creates a collection of related treatment contrasts. The registry reports a comparison for each listed regimen, but does not describe multiplicity handling. This distinction matters: a set of individually reported p-values is not necessarily equivalent to a prespecified family of confirmatory tests.

Third, effect estimates, confidence intervals, and p-values answer different questions. The estimate conveys the direction and scale of the average contrast; the interval conveys precision; the p-value assesses compatibility with a null comparison under assumptions. Considering all three is more informative than focusing on whether a p-value crosses a conventional threshold.

Fourth, planning calculations should not be confused with retrospective power. The registry’s illustrations use explicit assumptions and alternative effect fractions, while the trial’s original design assumptions are not reported. Smaller target effects require larger planned groups under the same calculation framework. This distinction supports transparent planning without implying that the observed study had a particular achieved power.

Finally, this record shows why differences between a sponsor’s model-based analysis and a simple recalculation should be made explicit. Summary-statistic calculations offer a useful check, but the randomized crossover analysis is the more relevant inferential approach. When a discrepancy is identified, the sponsor’s own analysis takes precedence, while the scope of the available record remains part of the 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.

Several limitations specific to this trial constrain interpretation. The registry identifies a randomized crossover design and describes important mixed-model terms, but does not report the treatment sequences, washout details, or a carryover assessment. These details matter for evaluating how period and prior treatment may relate to measurements in a crossover study. The record also does not explain all reasons for different analysis counts among treatment labels.

The primary analysis required at least one post-baseline assessment and non-missing covariate data. Although the model specification is described, the handling of missing outcome data, incomplete periods, and sensitivity analyses is not reported in the registry record. The available information therefore does not establish how robust the findings are to alternative assumptions about missingness.

Many regimens were compared with placebo, yet the record does not state whether multiplicity adjustments or a testing hierarchy were used. The reported p-values and confidence intervals should be interpreted with that uncertainty in mind. The simple recalculations are also approximate and unadjusted, so they cannot resolve questions about the full crossover model or replace the sponsor’s analysis.

The registry identifies secondary FEV1 outcomes, but numerical results for the serial FEV1 outcome are not reported in the registry record. Detailed secondary comparisons and pharmacokinetic results are likewise not included among the results. The record does not give a clinical-importance threshold for the primary FEV1 contrast, limiting assessment of the practical importance of the estimated differences.

Finally, this is a phase 2 study with a recorded enrollment of 176 and varying numbers contributing to individual treatment estimates. The registry record does not report the original sample-size justification or full statistical analysis plan. These limitations do not negate the posted estimates, but they narrow the conclusions that can be drawn from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: GSK573719 Dose Ranging Study in Chronic Obstructive Pulmonary Disease — NCT00950807.
• Registry record last updated 2017-11-08; status last verified 2017-10.
• Results first posted 2014-03-04.
• 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 record describes a completed, randomized, quadruple-masked, phase 2 crossover study of GSK573719 regimens in participants with COPD. It lists 176 participants overall and compares several once-daily and twice-daily doses with placebo; tiotropium is also included. The primary outcome is change from baseline in trough FEV1 at Day 15 of each treatment period.

The sponsor’s mixed-model comparisons report positive mean differences versus placebo for all listed treatment regimens, with 95% confidence intervals and p-values. A simple unadjusted recalculation produces close but not identical estimates; because the record indicates a discrepancy, the sponsor’s analysis takes precedence. The registry does not report the original sample-size assumptions, multiplicity handling, full missing-data procedures, or all crossover operational details.

The results describe average FEV1 changes in the analyzed population and do not establish individual responses, clinical importance, or effects on outcomes not reported in the registry record.