AMPLIFY - D6571C00001 Duaklir USA Phase III Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for AMPLIFY - D6571C00001 Duaklir USA Phase III Study (NCT02796677), a randomized phase 3 study. The primary outcome is Change From Baseline in 1-hour Morning Post-dose Dose Forced Expiratory Volume in 1 Second (FEV1) of AB/FF 400/12 μg Compared to AB 400 μg at Week 24.

2. Clinical Question

3. Trial Design

AMPLIFY (NCT02796677) was a Phase III, randomized, double-blind, double-dummy, parallel-group, multicenter study of treatments for stable chronic obstructive pulmonary disease. The registry lists enrollment of 1595 and status as completed. The listed study dates are 2016-07-05 for the start and 2017-06-08 for primary completion. The registry describes a 24-week treatment period.

Four treatment groups are listed: AB/FF 400/12 μg twice daily, AB 400 μg twice daily, FF 12 μg twice daily, and TIO 18 μg once daily. The combination and its individual components were administered by Pressair®/Genuair® inhaler, while TIO was administered by Handihaler®. Double-dummy masking means that the design used matching placebo treatment alongside active treatment; the registry lists placebo interventions for the combination and component treatments and for TIO. This design feature is consistent with comparing regimens that differed in their active treatment and dosing schedule while maintaining masking.

The primary comparison was AB/FF against AB. The posted primary analysis population is described as the intention-to-treat population: randomized participants who took at least one dose and had at least a baseline FEV1 measurement, regardless of adherence to randomized treatment. The record also reports comparisons involving FF and TIO in the posted arm summaries, but the primary endpoint title identifies AB as the comparator. The original trial’s detailed allocation procedure, its planned statistical analysis plan, sample-size justification, and original design assumptions are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Eligible Participants signed informed consent form (ICF) \& entered screening (Run-in) period (14 ± 3 days), inclusion/exclusion criteria were checked by medical \& COPD history, physical examination, laboratory analysis, electrocardiogram, \& COPD severity (COPD Assessment Test \[CAT\] \& post-bronchodilator forced expiratory volume in 1 second \[FEV1\])

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention-to Treat (ITT) population: All randomized participants who took at least one dose of IP and had at least a baseline FEV1, under the ITT principle and regardless the adherence to the randomized treatment.

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 1-hour Morning Post-dose Dose Forced Expiratory Volume in 1 Second (FEV1) of AB/FF 400/12 μg Compared to AB 400 μg at Week 24, measured over At baseline 1-hour postdose and Week 24.

The primary endpoint is change from baseline in FEV1 measured 1 hour after the morning dose at Week 24. FEV1 is the volume of air that can be forcibly exhaled in the first second of a forced expiration, and the registry reports the change in litres. In general, FEV1 is used as a measure of airflow limitation and can provide a way to compare lung-function response between randomized treatment groups.

The endpoint is a continuous measure, so the posted arm results are least-squares means rather than counts of participants with or without an event. The registry defines baseline as the average of two FEV1 values measured immediately before the first dose at randomization; if one of the two measurements was missing, the available measurement was used as baseline. The stated timeframe includes baseline and Week 24.

The primary analysis focuses on the difference between the combination and AB monotherapy. The registry reports a mixed model for repeated measures analysis of that comparison. Such models are commonly used for repeated measurements over time, but details of the model specification and its missing-data assumptions are not reported in the registry record. The endpoint therefore describes the mean measured change in lung function under the recorded analysis, not every participant’s individual response and not a patient-reported outcome.

7. Results Posted in the Registry

• AB 400 μg: mean 0.17 versus 0.25 on control; difference -0.08 (95% CI -0.12 to -0.05), standardized effect d = -0.36; z-test p = <0.001.
• FF 12 μg: mean 0.17 versus 0.25 on control; difference -0.08 (95% CI -0.12 to -0.05), standardized effect d = -0.37; z-test p = <0.001.
• TIO 18 μg: mean 0.16 versus 0.25 on control; difference -0.09 (95% CI -0.13 to -0.06), standardized effect d = -0.39; 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 in Normalized Area Under Curve 3hours Post-dose (nAUC0-3/3h) FEV1 of AB/FF 400/12 μg Compared to AB 400 μg and and FF 12 μg at Week 24

• 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:
  • AB 400 μg: mean 0.16 versus 0.24 on control; difference -0.07 (95% CI -0.11 to -0.04), standardized effect d = -0.34; z-test p = <0.001.
  • FF 12 μg: mean 0.15 versus 0.24 on control; difference -0.09 (95% CI -0.12 to -0.05), standardized effect d = -0.38; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for AB 400 μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for FF 12 μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts secondary outcomes covering normalized post-dose FEV1 area under the curve and SGRQ total-score responder status. The secondary lung-function summaries show a pattern in which the combination group’s reported mean change is greater than the corresponding component-group summaries. The sponsor’s posted repeated-measures analyses for the reported combination comparisons also have positive LS mean differences and confidence intervals above zero. These outcomes are broadly aligned with the primary lung-function result, but they measure a different time profile or comparison and should not be treated as interchangeable with the primary endpoint.

The SGRQ outcome is listed as a responder analysis, which concerns the number of participants meeting a responder definition rather than a continuous FEV1 change. The registry record does not provide a posted result for this outcome in the information available for this analysis, so its direction and magnitude cannot be characterized. A listed outcome should not be mistaken for a reported finding.

Secondary results generally carry less weight than the prespecified primary question because there may be multiple outcomes, comparisons, and analysis opportunities. Testing many hypotheses increases the chance that some results appear statistically persuasive by chance unless an appropriate multiplicity strategy is planned and applied. The registry record does not report whether adjustment was used, how the secondary hierarchy was defined, or whether these analyses were confirmatory. Accordingly, the secondary pattern can provide context and consistency, but should not be used to make claims as strong as those based on a clearly identified primary analysis. The primary finding remains the central result; secondary evidence is supportive in description, with inferential certainty limited by what is reported.

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

• Change From Baseline in Normalized Area Under Curve 3hours Post-dose (nAUC0-3/3h) FEV1 of AB/FF 400/12 μg Compared to AB 400 μg and and FF 12 μg at Week 24
• Responder (Number of Participants) Analysis of St. George's Respiratory Questionnaire (SGRQ) Total Score With AB/FF 400/12 μg Versus AB 400 μg and FF 12 μg.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a measured amount of FEV1 change, expressed in litres. For a continuous outcome, an arm summary such as a least-squares mean describes the group’s estimated average change. A mean difference compares the estimated averages between groups. In general, a difference near zero indicates similar group averages, while the direction indicates which group has the larger value according to the contrast’s defined ordering. The registry reports the sponsor’s primary contrast as a positive difference for AB/FF relative to AB.

What does a mixed model for repeated measures do?

In general, a mixed model for repeated measures analyzes outcome measurements collected at multiple occasions while accounting for their relationship within a participant. It can estimate group means and between-group differences over time while using the repeated measurements available to the model. The registry identifies this method for the primary comparison and reports an LS mean difference, confidence interval, and p-value. It does not report the full model specification, such as its covariates, covariance structure, or detailed handling of missing measurements. Those details should not be inferred from the method name alone.

Least-squares means are model-based estimates of group means. They may differ from simple arithmetic averages because they come from a statistical model. For that reason, the sponsor’s reported primary estimate should not be treated as interchangeable with a subtraction made from the posted arm summaries. The unadjusted recalculations use those summaries and are useful as a check on broad direction and scale, but they do not reproduce the sponsor’s model.

What does a p-value convey?

In general, a p-value measures how incompatible the observed data are with a specified statistical null model, assuming that model and the analysis are appropriate. It is not the probability that the null hypothesis is true, and it does not measure the probability that a result is due to chance in a general sense. The sponsor reports p < 0.001 for the primary comparison. This is evidence against a zero difference under the reported model, but it does not quantify clinical importance, establish causation beyond the randomized study’s scope, or remove uncertainty about the estimate’s size.

The registry also shows unadjusted recalculated p-values for comparisons derived from posted arm summaries. These are not the same analysis as the sponsor’s repeated-measures model. Such summary-statistic calculations do not account for the trial’s full data structure or any model adjustment, and therefore should not replace the sponsor’s analysis where that analysis is reported.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variability is greater than a statistical model expects. A model that underestimates variability may produce confidence intervals that are too narrow and p-values that are too small. This concept is most relevant when outcomes are counts or binary events and the assumed variance structure does not fit the data. The primary endpoint is continuous, and the registry reports standard errors for its arm estimates. It does not report an over-dispersion assessment or enough model details to evaluate one. Over-dispersion should therefore not be asserted as a finding of this trial.

The standard errors attached to arm-level least-squares means describe uncertainty in those estimated means. They are not standard deviations of individual participant measurements. A standard deviation describes spread among observations, whereas a standard error describes precision of an estimated quantity. This distinction matters when interpreting the posted summaries and when considering the approximate pooled standard deviations used for the separate unadjusted calculations.

What do the effect-size re-calculations represent?

The posted unadjusted re-calculations use group summary values to derive an approximate between-group contrast and standardized effect size. They are simple re-calculations, not sponsor analyses. The pooled standard deviation is approximate because the arm-level information includes standard errors rather than individual-level data. These derived quantities can help describe the scale of a contrast relative to variability, but they do not account for the repeated-measures model, covariate adjustment, or multiplicity. The reported sponsor estimate remains the more relevant inferential result for the primary endpoint.

Randomization and masking are design protections against systematic differences in treatment assignment and expectations. In general, random allocation supports causal comparison when the trial is conducted and analyzed appropriately; masking can reduce some forms of expectation-related bias. The registry identifies the study as randomized and double-blind, double-dummy, but details of sequence generation, concealment, and implementation are not reported in the registry record. These design labels are informative, but they do not by themselves answer questions about adherence, attrition, missing data, or all possible sources of bias.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is an LS mean difference of 0.084 litres, with a 95% confidence interval from 0.051 to 0.117 litres. In general, a confidence interval gives a range of values reasonably compatible with the data and the statistical model, with the stated confidence level describing the long-run behavior of the interval procedure under its assumptions. It is not a range guaranteed to contain the true effect, and it does not account for biases or model misspecification.

The primary interval lies above zero, matching the reported direction of the contrast. Its lower and upper limits convey uncertainty about the magnitude: the data are compatible with a range of positive differences, rather than identifying one exact value. The interval’s width reflects statistical precision under the sponsor’s analysis; precision is distinct from clinical importance. The registry record does not report a threshold against which to judge whether a difference of this size is clinically important.

The arm-level standard errors are 0.013 litres for AB/FF and 0.011 litres for AB. These describe precision of the estimated arm means, not the spread of individual FEV1 changes. The reported confidence interval comes from the sponsor’s mixed model for repeated measures and should be preferred to intervals derived from the separate unadjusted summary-statistic calculations.

Confidence intervals depend on the analysis assumptions and available data. The registry record does not report enough detail to assess the model’s full specification or the handling of missing follow-up measurements. Nor does an interval address multiplicity across the several posted outcomes and comparisons. Consequently, the primary interval is most directly interpreted as precision for the reported primary contrast under the stated model, not as a complete account of every source of uncertainty.

12. Planning a Similar Trial: Sample Size

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

The sample-size display is a planning illustration based on the observed effect, not the trial’s original design calculation. Its figures are participants per arm for comparisons of two groups; they are not total event counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design that would have an 80% chance of detecting the specified effect under those assumptions, if the effect and model assumptions held. The 90% power column gives the corresponding planning target for a higher chance of detection. Power is a property of a hypothetical study design under assumptions; it is not a measure of how likely the result already observed is to be true.

Rows that plan for a smaller fraction of the observed effect require more participants per arm than rows that plan for the full observed effect. This reflects a general statistical principle: smaller group differences are harder to distinguish from random variation, so larger studies are generally needed to detect them with the same planned power. Estimates based on an observed effect can be optimistic if that effect is imprecise or unusually large, and the calculation does not establish that the original study was designed around the displayed assumptions. This is not observed power.

The curve should be read as another view of the same planning relationship between assumed effect size and required participants per arm. It is an illustration based on the specified assumptions, not a report of actual enrollment targets or a reconstruction of the original protocol’s sample-size rationale.

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 = -0.084; pooled standard deviation σ = 0.236.
2. n = 2 × (1.96 + 0.842)² × 0.236² / -0.084² = 124.0, rounded up to 124 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 <- -0.084                      # observed difference in means
sigma <- 0.236053985598421                     # 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(2796677)
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 = 124 (80% power), 166 (90% power)
 75% of observed effect: n per arm = 221 (80% power), 296 (90% power)
 50% of observed effect: n per arm = 496 (80% power), 664 (90% power)
power.t.test: 124.9 
Simulated power at n = 124 per arm: 0.805 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis uses a mixed model for repeated measures and reports an LS mean difference of 0.084 litres for AB/FF compared with AB, with a 95% confidence interval from 0.051 to 0.117 litres and p < 0.001. This is the trial’s own inferential result for the primary comparison.

The unadjusted recalculation is based on the posted arm-level summary statistics. It is a separate, simpler calculation and does not reproduce the repeated-measures model. Its direction and approximate magnitude are consistent with the sponsor’s reported result. The registry record does not flag a discrepancy. If a discrepancy were present, the sponsor’s own analysis would take precedence for describing the trial’s reported analysis; in this record, the sponsor result is still the preferred primary estimate because it reflects the stated model rather than an unadjusted reconstruction.

Agreement between the two approaches is a useful consistency check, not proof that they share identical assumptions or answer every analysis question. The sponsor’s interval and p-value should be used when discussing the primary modeled comparison. The recalculation is best treated as a transparent approximate check from the arm summaries, not as a replacement or independent confirmation based on participant-level data.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several statistical hypotheses are evaluated, such as multiple treatment comparisons or multiple endpoints. In general, the more hypotheses examined, the greater the chance of at least one apparently unusual result if all null hypotheses are true. Methods such as hierarchical testing or adjustment can control error rates, but the method must be specified and interpreted in context. The registry record lists several outcomes and comparisons but does not report a multiplicity procedure or a testing hierarchy. The unadjusted secondary p-values therefore should not be treated as though they necessarily preserve the error rate of a single primary test.

The primary analysis population is described as the intention-to-treat population: randomized participants who took at least one dose and had at least a baseline FEV1 measurement, regardless of adherence to randomized treatment. This is the registry’s stated definition, and it should not be assumed to include every randomized participant. The record does not report the number excluded from this analysis population or the reasons for any exclusions.

The primary endpoint description states how baseline was set when one of the two pre-dose FEV1 values was missing. That is a baseline-measurement rule, not a complete account of missing Week 24 measurements or other follow-up data. The reported repeated-measures method can use repeated observations, but the model’s missing-data assumptions and any sensitivity analyses are not reported in the registry record. It is therefore not possible to judge from the record whether missing outcome data could have affected the estimate or how robust the finding is to alternative assumptions.

The statistical analysis plan, protocol deviations, details of adherence, and sensitivity analyses are not reported in the registry record. These omissions limit assessment of whether the reported analysis fully followed the original plan and how conclusions might change under other reasonable methods. They do not invalidate the posted result, but they define the boundaries of what can be concluded from the registry information.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% 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 (3.1%), pneumonia (1.3%), myocardial infarction (0.6%), cardiac failure acute (0.4%), cardiac failure congestive (0.4%).

The registry reports serious adverse events as counts among participants at risk in each treatment group. The recorded counts are 23 of 314 for AB/FF, 41 of 475 for AB, 22 of 319 for FF, and 37 of 475 for TIO. Other adverse events are reported separately as 173 of 314, 222 of 475, 178 of 319, and 241 of 475, respectively. The record also lists deaths as 1, 1, 4, and 2 in the same treatment-group order.

These are descriptive figures, not estimates of causal treatment effects. The counts alone do not adjust for exposure time, differences in participant characteristics, or uncertainty in between-group comparisons. A serious adverse event is not necessarily judged to have been caused by treatment. The registry lists chronic obstructive pulmonary disease (3.1%), pneumonia (1.3%), myocardial infarction (0.6%), acute cardiac failure (0.4%), congestive cardiac failure (0.4%), and atrial fibrillation (0.4%) among the top serious-event terms. These percentages should be read as posted event-term summaries; the record does not provide enough detail to interpret them as comparative risks or treatment-attributable rates.

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

The primary finding is a reported difference between randomized groups in mean change in morning post-dose FEV1 at Week 24. The sponsor’s repeated-measures analysis estimates a larger mean change for AB/FF than for AB, and its confidence interval is above zero. This is evidence of a group-level difference for the defined outcome and analysis population in this study.

The result does not imply that every participant had a greater response with the combination, nor does a difference in group means describe the full range of individual responses. It is not a direct measure of symptoms, daily functioning, exacerbations, or quality of life. A secondary SGRQ responder outcome is listed, but the corresponding result is not available in the posted information. The registry record also does not state a clinical-importance threshold for the primary FEV1 difference, so statistical evidence should not be equated with a judgment about patient importance.

The study’s randomized, masked design supports comparison of the assigned regimens, but the registry summary does not provide all details needed to evaluate implementation, missing data, multiplicity, or the full analysis plan. The confidence interval reflects uncertainty under the sponsor’s model and does not cover every possible bias or limitation. Nor does a low p-value establish the probability that the treatment effect is real or that the same estimate would occur in another population.

Safety findings are also descriptive. Counts of serious events, other events, and deaths do not by themselves establish whether one regimen is safer, and the listed serious-event terms do not establish treatment causation. The registry results should therefore be understood as evidence about measured trial outcomes, with their scope and uncertainty, rather than as a complete assessment of clinical benefit or harm.

18. Why This Trial Matters Statistically

This trial illustrates why the distinction between a sponsor’s modeled estimate and a simple summary-statistic recalculation matters. The primary comparison was analyzed with a mixed model for repeated measures, while the posted arm summaries permit only an unadjusted approximate check. Those analyses can be consistent in direction without being methodologically interchangeable. Readers should give the sponsor’s reported model result priority when describing the trial’s primary inferential analysis.

It also shows the value of reading an effect estimate alongside its confidence interval rather than relying on a p-value alone. The interval communicates uncertainty about the magnitude, whereas the p-value addresses compatibility with a null model. Neither statistic establishes clinical importance, which requires context not stated in the registry record.

Finally, the record distinguishes a clearly identified primary endpoint from several secondary outcomes and comparisons. That distinction matters because results across multiple tests have different evidential weight, especially when the multiplicity strategy is not reported. Planning illustrations based on an observed effect can help explain how sample size depends on the effect one hopes to detect, but they do not reveal the original trial’s design rationale or observed power. Together, these issues make the study a useful example of how trial design, model choice, precision, multiplicity, and reporting completeness shape statistical 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 trial-specific limitations of interpretation follow from the registry information. First, the record does not report the full statistical analysis plan or the detailed repeated-measures model specification. Covariate adjustment, covariance structure, and handling of missing follow-up measurements therefore cannot be assessed from the posted record. The analysis population is defined as randomized participants who took at least one dose and had a baseline FEV1 measurement, but the record does not state the number or reasons for exclusions from that population.

Second, the registry lists multiple outcomes and comparisons without reporting a multiplicity strategy. The primary comparison is identifiable, but the strength of inference for secondary comparisons is harder to judge when the testing hierarchy and any adjustment are unknown. The SGRQ responder outcome is listed, but a corresponding result is not included in the posted outcome information.

Third, the posted arm summaries are not participant-level data. The recalculations are approximate and unadjusted, and the pooled variability used for them is itself approximate. They cannot reproduce the sponsor’s model or support an independent assessment of assumptions, outliers, or distributions. The sponsor’s reported primary analysis is therefore the more appropriate estimate for the primary question.

Finally, the registry information does not state a clinical-importance threshold for the FEV1 difference and does not provide sufficient detail to interpret adverse-event counts as comparative risks. The record describes a specific population, treatment period, endpoint, and analysis; generalization beyond that setting requires evidence not reported in this record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: AMPLIFY - D6571C00001 Duaklir USA Phase III Study — NCT02796677.
• Registry record last updated 2018-11-09; status last verified 2018-11.
• Results first posted 2018-11-09.
• 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

NCT02796677 is the completed Phase III AMPLIFY study of AB/FF and comparator regimens in people with stable COPD. It was randomized, double-blind, double-dummy, and parallel-group, with a 24-week treatment period and registry enrollment of 1595.

The primary endpoint was change from baseline in 1-hour morning post-dose FEV1 at Week 24. The sponsor’s mixed-model analysis reported an LS mean difference of 0.084 litres for AB/FF compared with AB, with a 95% confidence interval from 0.051 to 0.117 litres and p < 0.001. The registry also posts secondary lung-function outcomes and descriptive safety counts.

The result is a group-level estimate under the reported analysis. Details of the original sample-size rationale, full statistical plan, multiplicity handling, and missing follow-up data are not reported in the registry record.