Efficacy and Safety of Mepolizumab as an Add-on Treatment in Chronic Obstructive Pulmonary Disease (COPD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Mepolizumab as an Add-on Treatment in Chronic Obstructive Pulmonary Disease (COPD) (NCT02105961), a randomized phase 3 study. The primary outcome is Rate of Moderate or Severe Exacerbations.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, parallel-group trial with placebo control. The registry classifies masking as triple; the brief summary describes the study as double-blind. Which specific roles were masked is not reported in the registry record. The registry lists enrollment as 674, while the brief summary describes a planned randomization of 660 participants in a 1:1:1 ratio. These are different record statements and should not be treated as interchangeable measures of enrollment.

The three regimens were mepolizumab 100 mg, mepolizumab 300 mg, and placebo, each administered by subcutaneous injection every 4 weeks. The active treatments were added to baseline COPD medication. The planned treatment period was 52 weeks, with an approximately 62-week participation period described in the brief summary, including screening and follow-up. The registry records the study start as 2014-04-24, primary completion as 2017-01-16, and status as completed.

The primary analysis used the modified intent-to-treat population, defined in the endpoint description as randomized participants who received at least one dose. The posted arm counts for the primary outcome were 226 for placebo, 223 for mepolizumab 100 mg, and 225 for mepolizumab 300 mg. The record also lists secondary outcomes concerning time to first moderate/severe exacerbation, exacerbations requiring emergency department visits and/or hospitalizations, SGRQ score, and CAT score. The original protocol’s detailed allocation procedures, eligibility criteria beyond those described in the brief summary, and statistical 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: A total of 674 participants were randomized and received at least one dose of study treatment and were included in the modified intent to treat (mITT) population. One participant randomized to the mepolizumab 300 mg group was withdrawn without receiving study treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: mITT Population

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Rate of Moderate or Severe Exacerbations, measured over From randomization to Week 52.

The primary endpoint was the rate of moderate or severe COPD exacerbations per year, assessed from randomization to Week 52. It counts qualifying episodes over follow-up, so it represents the frequency of exacerbations rather than simply the proportion of participants who experienced at least one event. Moderate exacerbations were defined as clinically significant events requiring oral/systemic corticosteroids and/or antibiotics. Severe exacerbations were defined as events requiring inpatient hospitalization for at least 24 hours or resulting in death.

The registry says that events from the start of investigational product through the Week 52 visit were included. It also included exacerbations reported after early discontinuation of investigational product when participants remained in the study. The measure is expressed as events per year, and the posted group results are least-squares means with 95% confidence intervals.

A rate endpoint is useful when participants can experience repeated events and may contribute different amounts of observed follow-up. It summarizes event frequency in relation to exposure time, unlike a binary endpoint that records only whether an event occurred. This general distinction matters when interpreting the results: a rate comparison concerns the event burden over follow-up and does not, by itself, describe the probability that any individual participant will experience an exacerbation. The precise sponsor model and its handling of all analysis details are discussed through the registry’s reported methods; details not stated there are not reported in the registry record.

7. Results Posted in the Registry

• Mepolizumab 100 mg SC: 1.19 versus 1.49 (Moderate/severe exacerbations per year) on control; rate ratio 0.80 (95% CI 0.65–0.98, derived from the posted confidence limits); p ≈ 0.035.
• Mepolizumab 300 mg SC: 1.27 versus 1.49 (Moderate/severe exacerbations per year) on control; rate ratio 0.85 (95% CI 0.69–1.05, derived from the posted confidence limits); p ≈ 0.136.

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 Mean Total St. George's Respiratory Questionnaire (SGRQ) Score

• 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:
  • Mepolizumab 100 mg SC: mean -5.00 versus -3.10 on control; difference -1.90 (95% CI -4.58 to 0.78), standardized effect d = -0.13; z-test p = 0.164.
  • Mepolizumab 300 mg SC: mean -3.30 versus -3.10 on control; difference -0.20 (95% CI -2.89 to 2.49), standardized effect d = -0.01; z-test p = 0.884.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Mepolizumab 100 mg SC and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Mepolizumab 300 mg SC and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Mean COPD Assessment Test (CAT) Score

• 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:
  • Mepolizumab 100 mg SC: mean -1.60 versus -0.40 on control; difference -1.20 (95% CI -2.36 to -0.04), standardized effect d = -0.19; z-test p = 0.043.
  • Mepolizumab 300 mg SC: mean -0.80 versus -0.40 on control; difference -0.40 (95% CI -1.56 to 0.76), standardized effect d = -0.06; z-test p = 0.501.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Mepolizumab 100 mg SC than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Mepolizumab 300 mg SC and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies secondary outcomes that span event timing, event severity and healthcare use, and patient-reported respiratory health. Posted numerical results in the record include changes in SGRQ and CAT scores; results for time to first moderate/severe exacerbation and for exacerbations requiring emergency department visits and/or hospitalizations are not reported in the registry record.

Across the posted continuous outcomes, the estimates do not form a uniformly consistent pattern across both doses and both measures. The recalculated comparisons indicate a more pronounced difference from placebo for the 100 mg group than for the 300 mg group, while the sponsor’s repeated-measures results include estimates and p-values that do not always align with the simple recalculations. The SGRQ and CAT outcomes measure different aspects of respiratory health from the primary recurrent-event rate, so they are complementary rather than interchangeable evidence.

Secondary results generally carry less inferential weight than the primary endpoint when many outcomes, doses, time points, or comparisons are examined. Multiple testing increases the chance that at least one result will appear notable by chance if no adjustment or hierarchy is used. The registry does not report the prespecified multiplicity strategy or enough analysis-plan detail to determine how these secondary tests were controlled. The recalculated secondary p-values are explicitly unadjusted and should not be treated as confirmatory findings. The sponsor’s reported secondary analyses take precedence over simple recalculations, but the record’s duplicated entries and differing p-values call for caution where present.

The secondary pattern therefore adds context, not a single definitive verdict that overrides the primary analysis. No overall claim across all registered secondary outcomes is possible because some endpoint results and the multiplicity plan are not reported in the registry record.

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

• Time to First Moderate/Severe Exacerbation
• Rate of COPD Exacerbations Requiring Emergency Department (ED) Visits and/or Hospitalizations (Hosp)
• Change From Baseline in Mean Total St. George's Respiratory Questionnaire (SGRQ) Score
• Change From Baseline in Mean COPD Assessment Test (CAT) Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a count rate: participants may have more than one qualifying exacerbation, and observed follow-up can differ. A rate model therefore addresses event frequency rather than treating each participant as having only one yes-or-no outcome. The registry reports that the sponsor used a negative binomial model for the primary comparisons.

Why use a negative binomial model?

In general, count data can vary more than a simple Poisson model expects. This is called over-dispersion: the observed counts are more variable than the model’s basic mean-variance relationship allows. A negative binomial model can accommodate this extra variation by including a dispersion component. That can be relevant for recurrent clinical events, because participants’ event counts may differ substantially. The registry names the negative binomial model but does not report its full specification, covariates, dispersion estimate, or detailed assumptions. Those elements are not reported in the registry record.

The reported rate ratio compares the estimated event rates between an active-treatment group and placebo. A ratio of 1.00 corresponds to equal rates; a value below 1.00 indicates a lower estimated rate in the numerator group, and a value above 1.00 indicates a higher estimated rate. This is a general interpretation of a rate ratio, not a claim about an individual participant’s outcome. The sponsor’s reported values are rounded to two decimal places, while the separate recalculations use posted summary statistics and are not the sponsor model’s estimates.

What does the confidence interval add?

A confidence interval describes the uncertainty around an estimate under the method used to construct it. A narrower interval indicates greater precision than a wider interval, all else equal. For a rate ratio, an interval spanning 1.00 is compatible with equal rates as well as with values on either side of that reference, at the stated confidence level. It should not be read as a range that contains a known fixed proportion of individual outcomes. The primary sponsor intervals are reported at the 95% level.

The recalculated comparisons are labelled unadjusted because they are simple comparisons derived from posted summary statistics, rather than the sponsor’s full negative binomial model. The recalculation also uses an interval-based approach and exposure-time information described in the record. It does not reproduce unreported modeling choices or account for any adjustments that may have been part of the sponsor’s analysis. In this trial the discrepancy flag is true, so the sponsor’s own analysis takes precedence over these recalculations.

Why can different p-values appear with the same estimate?

A p-value depends on the test procedure and its assumptions, not only on the displayed point estimate. Different analysis specifications or testing procedures can yield different p-values even when estimates and confidence intervals look similar. The registry lists two 100 mg superiority entries with the same rounded rate ratio and interval but different p-values, 0.068 and 0.034. It does not explain why. The entries for 300 mg both report p = 0.140. The source of the differing 100 mg p-values and whether either represents a particular multiplicity adjustment are not reported in the registry record. The values should therefore be reported as recorded rather than resolved by speculation.

For the continuous secondary endpoints, the registry reports least-squares mean changes and standard errors, with sponsor analyses described as mixed model repeated measures analyses. In general, repeated-measures models use measurements across visits and can account for the correlation of observations from the same participant. The registry does not give the model’s full specification, visit structure, covariance assumptions, or missing-data handling. A standard error describes uncertainty in an estimated mean; it is not the same quantity as the standard deviation of individual scores.

Some simple recalculations for continuous outcomes infer variability from the posted standard errors and arm sizes, using an approximate pooled standard deviation. Such recalculations are not the sponsor’s repeated-measures model and should be treated as rough, unadjusted comparisons. General statistical concepts can clarify the outputs, but the record does not provide enough detail to verify all model assumptions or reproduce the sponsor analyses.

What is the analysis population?

The registry defines the primary modified intent-to-treat population as randomized participants who received at least one dose of study treatment. The event analysis included qualifying events from treatment start through the Week 52 visit, including events after early treatment discontinuation for participants who remained in the study. The record does not provide a detailed account of participants excluded from each analysis, missing data, censoring, or sensitivity analyses. These details are not reported in the registry record.

11. Confidence Intervals and Precision

The primary sponsor confidence intervals give a useful measure of the uncertainty in the estimated rate ratios. For mepolizumab 100 mg versus placebo, the reported rate ratio was 0.80 and its 95% confidence interval was 0.65 to 0.98. For mepolizumab 300 mg versus placebo, the rate ratio was 0.86 and its 95% confidence interval was 0.70 to 1.05. The first interval is reported wholly below 1.00, while the second includes 1.00. These statements describe the reported estimates and intervals; they do not resolve the inconsistent p-values listed for the 100 mg comparison.

The arm-level rate intervals also show uncertainty in each estimated rate: 1.29 to 1.72 for placebo, 1.02 to 1.38 for 100 mg, and 1.09 to 1.48 for 300 mg. Such intervals are not individual prediction ranges, and overlap or non-overlap between separate arm intervals is not a substitute for the direct comparison and its confidence interval.

Precision is limited by the information in the trial and by variation in recurrent event counts. A confidence interval expresses uncertainty under a particular analysis method; it does not account for every possible bias, model misspecification, or difference between the study population and other populations. The registry does not report a detailed precision or sample-size justification for the original design. The recalculated intervals are based on posted summaries and are not a substitute for the sponsor’s negative binomial analysis, particularly because the record flags a discrepancy.

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 figures are planning illustrations based on the observed effect, not the original trial design calculation. For the primary rate outcome and the continuous outcomes, the figures are participants per arm. The record’s planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each illustration considers an effect equal to the stated fraction of the observed effect. The original trial’s own sample-size assumptions are not reported in the registry record.

The 80% power column describes the illustrative number of participants per arm that would give an 80% chance of detecting the specified effect under those assumptions if that effect were the true one. The 90% power column uses a higher chance of detection and therefore generally requires more participants. These are prospective planning interpretations, not evidence about what the completed study was capable of detecting in reality. The figures do not show observed power.

Rows for 100%, 75%, and 50% of the observed effect ask how planning requirements change if the effect targeted is smaller than, or equal to, the observed estimate. Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions. This is why the illustrative requirements rise as the assumed effect becomes a smaller fraction of the observed effect. Very small observed differences can produce especially large planning estimates; those values should be read as consequences of the stated calculation, not as recommendations or as evidence that a future study must use that size.

For time-to-event calculations, the record says the figures represent total events under a Schoenfeld approach. That differs from the participant-per-arm interpretation used for the other outcomes. The posted secondary results discussed in the record are continuous outcomes and the primary outcome is a rate, so their planning illustrations are in participants per arm.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 1.4900; treatment rate λ₁ = 1.1900 events per patient-year; follow-up T = 1.00 years.
2. n = (1.96 + 0.842)² × (1/1.4900 + 1/1.1900) / (1.00 × [ln(0.799)]²) = 235.5, rounded up to 236 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
lambda0 <- 1.49                      # control rate, events per patient-year
lambda1 <- 1.19                      # treatment rate
tt      <- 0.996550402453047                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(2105961)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 236 (80% power), 316 (90% power)
 75% of observed effect: n per arm = 406 (80% power), 544 (90% power)
 50% of observed effect: n per arm = 887 (80% power), 1,187 (90% power)
Simulated power, Poisson counts, n = 236 per arm: 0.799
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.637

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The sponsor’s primary comparisons are based on a negative binomial model. The reported rate ratio for 100 mg versus placebo is 0.80, with a 95% confidence interval of 0.65 to 0.98. The registry lists two p-values for this comparison: 0.068 and 0.034. For 300 mg versus placebo, the sponsor reports a rate ratio of 0.86, a 95% confidence interval of 0.70 to 1.05, and p = 0.140 in both entries.

The separate recalculations use posted summary statistics and a simpler unadjusted method. They yield values close to the sponsor’s rounded rate ratios, but the p-values and exact intervals are not identical. A recalculation is not a reconstruction of the sponsor’s model and cannot settle the conflicting 100 mg entries. Since the record flags a discrepancy, the sponsor’s own analysis takes precedence.

The registry does not explain why the two 100 mg entries have different p-values, whether they represent different analysis populations or testing procedures, or which entry corresponds to a particular adjustment. Those details are not reported in the registry record. The safest reading is to preserve the sponsor results as recorded, note the internal inconsistency, and avoid choosing one p-value by inference. The sponsor analysis also does not turn the estimate into a statement about individual outcomes or establish broader clinical meaning beyond the studied endpoint and population.

15. Multiplicity, Missing Data and Analysis Populations

The study compares two active doses with placebo and includes a primary outcome alongside multiple secondary outcomes. In general, conducting multiple statistical tests can increase the chance of at least one apparently positive result arising by chance. Trials may address this through a prespecified hierarchy, adjustment procedure, or other control of the overall error rate. Which approach was planned for this study is not reported in the registry record.

The primary results include two sponsor entries for the 100 mg comparison with the same displayed rate ratio and confidence interval but different p-values, 0.068 and 0.034. The 300 mg comparison appears twice with p = 0.140. The registry does not say whether these repeated entries correspond to different testing stages, populations, or adjustment methods. It is therefore not possible to identify a preferred multiplicity-adjusted p-value from the record alone. The discrepancy flag further means that the sponsor’s own analysis takes precedence over simple recalculations.

The primary analysis population is described as modified intent-to-treat: randomized participants who received at least one dose. The primary endpoint description includes events after early discontinuation of study treatment when the participant remained in the study. This is helpful detail, but it does not fully describe how missing observations, withdrawal from the study, incomplete follow-up, or other intercurrent events were handled. Missing-data methods, sensitivity analyses, and analysis populations for the secondary outcomes are not reported in the registry record.

The registry also does not report the original statistical analysis plan, detailed model specification, prespecified handling of multiplicity, or a sample-size justification. These omissions limit the ability to distinguish confirmatory tests from exploratory analyses and to assess the robustness of results to alternative assumptions. They do not invalidate the posted estimates, but they constrain how confidently the reported p-values can be interpreted as a coherent set of trial-wide evidence.

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 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 (16.4%), pneumonia (8.0%), infective exacerbation of chronic obstructive airways disease (2.2%), acute respiratory failure (1.3%), sepsis (1.3%).

The registry reports serious adverse events affecting 68 participants in the placebo group, 57 in the mepolizumab 100 mg group, and 60 in the mepolizumab 300 mg group. The corresponding group sizes at risk were 226, 223, and 225. The record also lists other adverse events affecting 137 participants with placebo, 147 with 100 mg, and 137 with 300 mg. Death counts were 9, 4, and 8, respectively.

These are descriptive counts in the posted safety record. They do not, by themselves, establish that a treatment caused or prevented an event. The serious adverse event terms listed most frequently overall include chronic obstructive pulmonary disease, pneumonia, infective exacerbation of chronic obstructive airways disease, acute respiratory failure, sepsis, and urinary tract infection. The record provides percentages for these terms but does not assign the listed term percentages to each treatment group in the information.

Safety comparisons require attention to event definitions, exposure, follow-up, and whether events are counted by participant or by event. The registry’s detailed safety-analysis methods and causal assessments are not reported in the registry record. These figures should therefore be read as counts reported by group, not as a causal comparison or medical advice.

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

The primary results describe estimated rates of moderate or severe exacerbations during the specified follow-up among the modified intent-to-treat population. They show lower estimated rates in both mepolizumab groups than in the placebo group, with the sponsor’s rate ratios and confidence intervals providing the direct comparisons. The 100 mg and 300 mg comparisons differ in their uncertainty, and the record contains conflicting p-values for the 100 mg comparison. The registry’s discrepancy flag means the sponsor’s own analysis takes precedence over unadjusted recalculations.

These findings do not show what would happen to every participant. A group rate is an average event frequency, and individuals may have different experiences. The outcome is limited to moderate and severe exacerbations as defined in the record and to events captured during the analysis period. It does not, by itself, establish effects on every aspect of COPD, quality of life, healthcare use, or long-term outcomes.

The secondary measures offer additional context but do not all point in a uniform direction, and their inferential weight is limited by the absence of a reported multiplicity plan. Some registered secondary outcome results are not reported in the registry record. Safety counts are also descriptive and cannot establish causation.

Interpretation is specific to the participants described in the study, the treatment regimens, the comparator, and the recorded analysis population. The results alone do not establish applicability to people who differ from the trial population. They are statistical evidence about the posted outcomes, not a treatment recommendation. The registry record does not provide enough detail to fully assess missing-data handling, all model assumptions, or the prespecified analysis strategy.

18. Why This Trial Matters Statistically

This trial illustrates several central issues in clinical biostatistics. First, the primary outcome is a recurrent-event rate, not a simple participant-level yes-or-no endpoint. Its analysis must account for the number of events and the time during which events were observed. A negative binomial model is a recognized way to analyze count rates when variability may exceed the simple Poisson pattern, although the registry does not report the complete model specification.

Second, estimates must be interpreted alongside their uncertainty. The rate ratio provides a relative comparison, while the confidence interval conveys precision under the analysis method. A point estimate alone can obscure how uncertain a comparison is, and a p-value does not convey effect size or clinical importance.

Third, sponsor analyses and summary-statistic recalculations answer related but not identical questions. The recalculations can be useful for checking approximate results, but they cannot reproduce unreported model details. The conflicting 100 mg p-values make transparent reporting especially important; the record flags a discrepancy, so the sponsor’s analysis takes precedence.

Finally, multiple endpoints and doses create multiplicity concerns. Secondary results need to be interpreted in the context of a prespecified strategy, which is not reported in the registry record. Together, these features show why sound interpretation depends not only on the numerical estimates, but also on the analysis population, endpoint definition, model, uncertainty, and completeness of the registry reporting.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The registry record leaves several trial-specific uncertainties. Although it identifies the primary endpoint and negative binomial model, it does not report the full model specification, covariates, dispersion estimate, or detailed assumptions. The sponsor’s entries for the 100 mg comparison have different p-values despite identical displayed rate ratios and confidence intervals, and no explanation is given. The record flags a discrepancy, so the sponsor’s own analysis takes precedence over simple recalculations.

The detailed statistical analysis plan, original sample-size justification, and multiplicity strategy are not reported in the registry record. This limits assessment of which comparisons were confirmatory and how the family of tests was controlled. Missing-data methods and sensitivity analyses are also not reported. The primary population is defined, and the event description clarifies that some events after treatment discontinuation were included, but this does not describe all follow-up and missingness decisions.

Some registered secondary outcomes do not have posted numerical results in the record. For the continuous outcomes, the sponsor used mixed model repeated measures analyses, while the simple recalculations rely on summary statistics and approximate variability. The recalculations cannot substitute for the sponsor model. The registry also differs between its enrollment figure and the planned randomization described in the brief summary; these statements refer to different record details and do not explain the difference.

Finally, the results apply to the eligibility description, treatment regimens, comparator, and follow-up captured in this trial. The record does not establish how well they generalize beyond that setting. These limitations affect certainty and scope of interpretation, rather than changing the posted values.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Mepolizumab as an Add-on Treatment in Chronic Obstructive Pulmonary Disease (COPD) — NCT02105961.
• Registry record last updated 2018-08-16; status last verified 2018-07.
• Results first posted 2018-04-06.
• 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

NCT02105961 was a completed Phase 3 randomized, parallel-group study of mepolizumab 100 mg or 300 mg versus placebo as add-on treatment for frequently exacerbating COPD. The primary outcome was the rate of moderate or severe exacerbations per year from randomization to Week 52 in the modified intent-to-treat population.

The sponsor reported lower estimated exacerbation rates for both active-dose groups than for placebo. Its 100 mg comparison has two posted p-values, 0.068 and 0.034, while the 300 mg comparison reports p = 0.140. Because the record flags a discrepancy, the sponsor’s analysis takes precedence over simple unadjusted recalculations. Secondary results, safety counts, confidence intervals, and planning illustrations add context, but missing analysis details and the unreported multiplicity strategy limit broader inference.