Efficacy of Fixed Combination of Beclometasone + Formoterol + Glycopyrrolate Versus Foster® in COPD: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of Fixed Combination of Beclometasone + Formoterol + Glycopyrrolate Versus Foster® in COPD (NCT01917331), a randomized phase 3 study. The primary outcome is 1_Change From Baseline in Pre-dose Morning Forced Expiratory Volume in the 1st Second (FEV1) -- at Week 26.

2. Clinical Question

In statistical terms, the primary endpoint compares adjusted average changes in lung function at a specified visit. The record reports an adjusted mean difference and its confidence interval, alongside the arm-level estimates. Those results describe the trial’s measured endpoint in its defined analysis population; they do not by themselves describe every outcome that may matter to patients or establish the size of a clinically important change. The registry record does not report a threshold for interpreting clinical importance.

3. Trial Design

This was a phase 3, randomized, parallel-group trial of the fixed beclometasone/formoterol/glycopyrrolate combination against beclometasone/formoterol (Foster®) in COPD. The record classifies allocation as randomized and the model as parallel. It classifies masking as quadruple, while the brief summary describes the study as double-blind. It also describes the trial as multicenter and multinational. The registry record does not identify the people or roles covered by its masking classification.

The record reports enrollment of 1368 and a study start date of 2014-03-21, with primary completion on 2016-01-14. The status is completed. The treatment period is described as 52 weeks. The primary endpoint was assessed at Week 26, with baseline identified as Week 0. The listed treatment regimens were CHF 5993 pMDI 100/6/12.5 µg, 2 inhalations bid, and Foster® 100/6 µg, 2 inhalations bid.

The primary efficacy analysis used an intention-to-treat population as defined in the record: randomized patients who received at least one dose and had at least one available post-baseline efficacy evaluation. For that outcome, the arm-level analysis counts were 642 and 616. These are analysis counts, not the overall enrollment figure. For the secondary exacerbation-rate outcome, the arm-level counts were 687 and 680. The registry record does not explain the difference in analysis counts between these outcomes, so they should not be treated as interchangeable denominators.

The design establishes a randomized comparison between the two assigned regimens, but the record excerpt does not give details such as the randomization procedure, allocation concealment, site count, or specific eligibility criteria. Those details are not reported in the registry record. Likewise, the record does not include a protocol-level account of treatment adherence or how treatment discontinuations were handled.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention-to-Treat (ITT) population: defined as all randomised patients who received at least one dose of the study treatment and with at least one available evaluation of efficacy (primary or secondary efficacy variables) after baseline.

5. Baseline Characteristics

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

Population: Safety population: all randomised patients who received at least one dose of the study treatment. One patient in the CHF 1535 pMDI group did not use the study medication kit provided at V2 and withdrew consent a few days after the visit.

6. Primary Endpoint

The registry lists the primary outcome as 1_Change From Baseline in Pre-dose Morning Forced Expiratory Volume in the 1st Second (FEV1) -- at Week 26, measured over Baseline (Week 0), Week 26..

The primary endpoint was change from baseline in pre-dose morning forced expiratory volume in the first second (FEV1) at Week 26. FEV1 is the volume of air a person can force out in one second after taking a deep breath. In this trial, the measurement was taken before the morning dose, which distinguishes it from a post-dose measurement and provides a specified point in the dosing schedule. The recorded unit was litre.

Change from baseline is used to describe how a measured value differs from its starting value over the study period. Comparing change between randomized groups focuses the question on the relative average change during the trial, rather than on either group’s endpoint value alone. The posted arm estimates are least-squares means, and the sponsor’s reported comparison is an adjusted mean difference from a linear mixed model for repeated measures.

FEV1 is a continuous measure, so the result is expressed as a difference in average change rather than as a count of participants meeting a response definition. The registry also lists secondary outcomes involving FEV1, symptoms, quality of life and COPD exacerbations. These measure different aspects of the trial and should not be treated as substitutes for the prespecified primary endpoint. The registry record does not report a threshold for a clinically important FEV1 change, so statistical evidence about the group contrast cannot, on its own, determine the clinical importance of its size.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: each participant’s FEV1 change is measured on a litre scale, and the reported arm summaries are least-squares means. A least-squares mean is a model-based estimate of an average, rather than necessarily the simple arithmetic mean of observed values. The registry reports an adjusted mean difference for the primary comparison, so the key inferential quantity is the model’s contrast between arms, not a subtraction reconstructed from the displayed arm summaries.

What does a confidence interval communicate?

A confidence interval expresses uncertainty around an estimated quantity under the analysis method. Here, the primary adjusted mean difference is 0.081 litre, with a 95% confidence interval from 0.052 to 0.109. The interval gives a range of values compatible with the observed data and the model at the stated confidence level. It is not a range containing a specified proportion of individual participants’ outcomes, and it does not establish the clinical importance of the estimate. The record’s interval for each arm-level least-squares mean describes uncertainty in that arm estimate; it should not be substituted for the interval on the between-arm contrast.

Why use a repeated-measures model?

The primary comparison was analyzed using a linear mixed model for repeated measures. In general, repeated-measures methods are used when measurements are collected across visits because observations from the same participant are related, rather than independent. A mixed model can use the structure of repeated observations to estimate the specified group contrast while accounting for within-participant association. The registry record does not report the exact model specification, covariance structure, covariates, estimation method or missing-data assumptions. Those elements should not be inferred from the model name alone.

The reported primary p-value is p < 0.001. In general, a p-value describes how incompatible the observed data are with a stated null hypothesis under the chosen model and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. The confidence interval is useful alongside the p-value because it shows the estimated direction and range of uncertainty for the adjusted contrast.

How should the rate analysis be understood?

A secondary outcome concerns the rate of moderate and severe COPD exacerbations over the treatment period. The sponsor’s reported analysis uses a negative binomial model and gives an adjusted rate ratio of 0.773, with interval limits 0.647 and 0.924, and p = 0.005. A rate ratio compares event rates between groups; it is not a difference in average FEV1 change or a proportion of participants. The registry does not state a confidence level for this comparison in a consistent way, so the interval is described by its reported limits without assigning a level.

In general, count outcomes can vary more than a simple Poisson model allows. This extra variability is called over-dispersion. A negative binomial model allows for such variability and is commonly used for event counts or rates when a Poisson assumption would be too restrictive. That general rationale does not establish why this specific model was selected: the model rationale and detailed specification are not reported in the registry record. The record also gives a separately calculated unadjusted rate comparison for planning illustrations. It should not be confused with the sponsor’s adjusted model result, because these analyses use different methods and answer differently specified questions.

What are the planning illustrations?

The accompanying sample-size section presents planning illustrations based on the observed secondary rate effect, with assumptions stated there. Such illustrations show how sample size would vary under those assumptions and chosen effect sizes. They are not observed power, do not establish the trial’s original design justification, and are not the trial’s actual enrollment results. The registry record does not report the trial’s own sample-size justification or the assumptions used when it was designed.

More generally, a statistical analysis plan determines which outcomes and contrasts are primary, how models are specified, and how uncertainty and multiplicity are handled. The registry record identifies the primary analysis method and gives the posted estimates, but does not provide a complete plan. Therefore, the results can be described as posted without assuming unreported modeling choices or treating the presented analyses as a complete account of all analyses conducted.

10. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis is the central comparison to interpret: a linear mixed model for repeated measures gives an adjusted mean difference of 0.081 litre, with a 95% confidence interval from 0.052 to 0.109 and p < 0.001. The registry also displays least-squares mean changes and confidence intervals for each arm. These summaries provide context for the reported contrast, but they do not contain all the information needed to reproduce the model-based adjusted estimate independently.

No separately recalculated two-arm primary contrast is reported. Accordingly, there is no independent primary re-calculation to set against the sponsor’s model result. The record marks the discrepancy status as false, and the sponsor’s analysis is the reported inferential comparison for this endpoint. This should not be read as independent validation of every model assumption; detailed specifications needed for that assessment are not reported in the registry record.

For the secondary exacerbation-rate outcome, the sponsor reports an adjusted rate ratio from a negative binomial model. The sample-size section’s unadjusted re-calculation is a distinct analysis based on posted summary statistics and is intended for planning illustration, not as a replacement for the sponsor’s adjusted analysis. When reporting the trial’s inferential result, distinguish the sponsor’s specified model from that unadjusted illustration.

11. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and posts a model and result for it, but it does not report a complete statistical analysis plan. In particular, multiplicity procedures for the secondary outcomes are not reported in the registry record. The record lists 19 outcome measures and 62 analyses, so there are multiple opportunities for inference across endpoints, visits and comparisons. Without a stated testing hierarchy or adjustment procedure, the secondary p-values should not all be treated as if they were independent confirmatory tests. The primary result has a clearer role because it is explicitly identified as the primary endpoint.

Missing-data handling is also incompletely described. The primary population definition requires at least one available post-baseline efficacy evaluation, but the registry record does not report how many primary observations were missing, why they were missing, or the assumptions and methods used for unavailable measurements. A repeated-measures model can use observed data under specified assumptions, but the model label alone does not reveal whether those assumptions are plausible in this trial. No sensitivity analysis for missing data is described, and the record does not state how intercurrent events or treatment discontinuation were handled.

The analysis population is not simply all enrolled patients: for the primary endpoint, it is defined as randomized patients who received at least one dose and had at least one post-baseline efficacy evaluation. The arm-level primary counts are 642 and 616. For the exacerbation-rate outcome, the posted counts are 687 and 680. Because the record does not explain the different counts, they should be considered outcome-specific rather than reconciled by assumption. The registry record does not report whether other analysis populations were used for additional endpoints or how those populations were defined.

These omissions do not erase the reported results, but they limit independent assessment of robustness and of the family of inferences across outcomes. The registry record does not report interim analyses, stopping rules, or the trial’s sample-size justification. No conclusions about these procedures should be inferred from the completed status or the posted p-values.

12. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: chronic obstructive pulmonary disease (11.0%), pneumonia (2.0%), myocardial ischaemia (0.6%), cardiac failure (0.6%), acute myocardial infarction (0.4%).

The safety summary reports serious adverse events for 106 of 687 participants in the beclometasone/formoterol/glycopyrrolate group and 123 of 680 participants in the beclometasone/formoterol group. It reports other adverse events for 181 of 687 and 203 of 680 participants, respectively. Deaths are reported as 15 and 16. These are the counts and denominators recorded for the two groups; they are not adjusted comparisons and should not be read as evidence that a treatment caused or prevented an event.

The listed serious-event terms include chronic obstructive pulmonary disease at 11.0%, pneumonia at 2.0%, myocardial ischaemia at 0.6%, cardiac failure at 0.6%, acute myocardial infarction at 0.4%, and myocardial infarction at 0.4%. The registry excerpt does not clarify the denominator or event-counting convention behind each listed percentage. It also does not provide a formal statistical comparison of safety outcomes. Serious-event counts, other adverse-event counts and deaths are different summaries; none alone captures the full clinical context, severity, timing or attribution of events. These figures describe what was posted in the registry record and are not a treatment recommendation.

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

The primary result describes an adjusted between-group difference in average change in pre-dose morning FEV1 at Week 26 among the analysis population defined in the registry. The reported estimate is 0.081 litre, with a 95% confidence interval from 0.052 to 0.109 and p < 0.001. It is evidence about this endpoint, time point, comparison and model. It does not mean every participant experienced the estimated average change, and it does not give the probability that a particular individual will have a specific outcome.

Statistical evidence and clinical importance are related but not interchangeable. The confidence interval and p-value summarize uncertainty and compatibility with a null comparison under the model. The registry record does not report a threshold for a clinically important FEV1 change, so this page cannot classify the size of the contrast as clinically important or unimportant. The primary result also does not by itself establish effects on symptoms, quality of life, exacerbations, survival or other outcomes.

The trial compared a fixed triple combination with Foster® in a randomized, parallel-group study described as 52 weeks of treatment. Results should be interpreted within that comparison and the reported follow-up. They do not establish how either regimen compares with treatments not included in the trial, or how findings apply to patient groups or settings not described in the record. The registry excerpt does not provide enough detail to assess all eligibility criteria or generalizability.

The safety summary is descriptive and does not establish causation. Likewise, the existence of additional outcome analyses does not mean all those findings are confirmatory; multiplicity handling is not reported. The registry record supports a precise description of the posted primary estimate, but leaves important questions about clinical thresholds, missing data, detailed model specifications and secondary-analysis procedures unresolved. These boundaries are part of the interpretation, not reasons to replace the posted result with an unsupported conclusion.

14. Why This Trial Matters Statistically

This trial illustrates why a headline result should be read together with its endpoint, analysis population and model. The primary question concerns a continuous spirometric measure at a particular visit. The reported adjusted mean difference directly compares average change between randomized groups, while arm-level estimates give useful context. Keeping those quantities distinct helps avoid treating separate confidence intervals as if they were the interval for the between-group contrast.

It also shows how modeling choices matter. The primary analysis uses a linear mixed model for repeated measures, while the secondary exacerbation-rate analysis uses a negative binomial model. These methods address different outcome structures: repeated continuous measurements in one case and event rates in the other. The estimates are therefore not interchangeable, even though both are comparisons between the trial arms.

The registry record also makes visible the gap between a posted statistical result and a complete account of the analysis. It identifies the primary model and reports its estimate, interval and p-value, but does not report a full statistical analysis plan, multiplicity procedure or detailed missing-data approach. This means that readers can accurately describe the primary result while remaining cautious about the broader family of secondary findings and the assumptions that cannot be checked from the record.

Finally, the trial’s planning illustrations should be separated from its observed evidence. Sample-size illustrations built from an observed effect are planning aids under stated assumptions, not observed power and not proof of how the original trial was designed. That distinction is useful whenever posted analyses include both trial results and hypothetical sample-size scenarios. Clear separation of observed estimates, adjusted sponsor analyses and illustrative re-calculations helps readers understand what each number can—and cannot—support.

15. Limitations

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

Several limitations are specific to what is available in this registry record. The primary result is reported, but the detailed linear mixed model specification is not. The record does not identify its covariates, covariance structure, estimation details or assumptions for missing observations. These omissions limit the extent to which an independent reader can reproduce or fully assess the adjusted estimate from the record alone.

The primary analysis population requires both receipt of at least one dose and at least one post-baseline efficacy evaluation. The record does not provide the number or reasons for missing primary measurements, or a sensitivity analysis addressing missingness. It also reports different analysis counts for the primary outcome and the exacerbation-rate outcome without explaining the difference. These features warrant care when comparing endpoint-specific summaries.

The registry excerpt does not report how multiplicity was handled across its outcome measures and analyses. This is particularly relevant when interpreting secondary results across several measures and visits. The record also does not give a clinical-importance threshold for the primary FEV1 endpoint, so statistical significance cannot be translated into a registry-based judgment about clinical importance.

Further details that are not reported in the registry record include the trial’s sample-size justification, interim analyses, detailed eligibility criteria, allocation procedures and the roles included in the masking classification. The summary describes the study as double-blind, while the record classifies masking as quadruple; the excerpt does not explain the terminology. These limitations concern the scope and transparency of the available record and should not be filled by assumptions about the protocol.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Efficacy of Fixed Combination of Beclometasone + Formoterol + Glycopyrrolate Versus Foster® in COPD — NCT01917331.
• Registry record last updated 2026-07-20; status last verified 2026-06.
• Results first posted 2026-06-03.
• 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.

19. Record Summary

The registry record describes NCT01917331, a completed phase 3 randomized parallel-group trial in COPD. It compares CHF 5993 pMDI, beclometasone/formoterol/glycopyrrolate, with Foster®, beclometasone/formoterol. Enrollment was 1368; the record gives a study start date of 2014-03-21 and primary completion date of 2016-01-14. Treatment is described over 52 weeks.

The primary endpoint was change from baseline in pre-dose morning FEV1 at Week 26. The reported repeated-measures analysis gives an adjusted mean difference of 0.081 litre, a 95% confidence interval from 0.052 to 0.109, and p < 0.001. Secondary outcomes include spirometry, exacerbation rates, dyspnoea and respiratory health status. Safety summaries report serious adverse events, other adverse events and deaths by group.

The record does not report a complete analysis plan, multiplicity procedures, detailed missing-data methods or a clinical-importance threshold for the primary endpoint. Those omissions limit interpretation beyond the posted analysis.