Placebo-controlled Efficacy and Safety Study of GSK3511294 (Depemokimab) in Participants With Severe Asthma With an Eosinophilic Phenotype: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Placebo-controlled Efficacy and Safety Study of GSK3511294 (Depemokimab) in Participants With Severe Asthma With an Eosinophilic Phenotype (NCT04719832), a randomized phase 3 study. The primary outcome is Annualized Rate of Clinically Significant Exacerbations up to 52 Weeks.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, double-blind, placebo-controlled, parallel-group, multicentre study of GSK3511294 (depemokimab) as adjunctive therapy. The registry lists asthma as the condition and describes the intended population as adults and adolescents with severe uncontrolled asthma with an eosinophilic phenotype. The study was completed, with enrollment of 395 participants.

The treatment period was 52 weeks. The intervention group received a 100 milligram subcutaneous dose at week 0 and week 26; the placebo group received injections on the same schedule. Participants in both groups were to remain on their existing baseline maintenance asthma standard-of-care treatment during the study. Thus, the comparison concerned the assigned study intervention in addition to ongoing baseline treatment, not a comparison of study injections without background treatment.

The primary outcome was the annualized rate of clinically significant exacerbations through Week 52. Seven outcome measures and six analyses are listed in the registry record. The posted secondary outcomes include changes in respiratory questionnaire and asthma-control scores, lung function and symptom diary scores, as well as exacerbations requiring hospitalization and/or an emergency department visit. Results are available for some, but not all, of those listed secondary outcomes.

The primary analysis counts were 132 for placebo and 249 for GSK3511294. The safety record lists 132 and 250 participants at risk in those groups, respectively. Those counts belong to different posted analyses and should not be treated as interchangeable. Further details of the original allocation ratio, the trial’s sample-size justification and the protocol’s full statistical plan 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 395 were randomized in the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The FAS included all randomized participants who received at least one dose of study intervention excluding participants from 1 site with GCP violation. Participants were analyzed according to the intervention they were allocated at randomization. Only those participants who were measured and analyzed (i.e., contributed data reported in the table) were included in the Overall Number of Participants Analyzed field. 'Number Analyzed' signifies participants evaluable for specified time points.

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: Full analysis set population included all randomized participants who received at least one dose of study intervention excluding participants from 1 site with GCP violation. Participants were analyzed according to the intervention they were allocated at randomization.

6. Primary Endpoint

The registry lists the primary outcome as Annualized Rate of Clinically Significant Exacerbations up to 52 Weeks, measured over Up to Week 52.

The primary endpoint was the annualized rate of clinically significant exacerbations up to Week 52, expressed as exacerbations per participant per year. The registry defined a clinically significant exacerbation as worsening asthma requiring systemic corticosteroids and/or hospitalization and/or an emergency department visit. For participants not on maintenance systemic corticosteroids, the definition required at least 3 days of intravenous or oral steroids, or a single intramuscular corticosteroid dose. For participants on maintenance systemic corticosteroids, it required at least double the existing maintenance dose for at least 3 days. Exacerbations separated by less than 7 days were treated as a continuation of the same event. Exacerbations recorded in the electronic case report form were considered verified and included in the primary analysis.

General statistical context: a rate endpoint represents how often events occur over participants’ observation time, rather than simply whether each participant ever had an event. Annualizing the rate gives a common time scale for comparing event frequency when participants contribute follow-up. Recurrent-event outcomes can contain more variation than a simple count model expects, a property called over-dispersion. A negative binomial model is one method used for event-rate comparisons that can allow for this extra variation. The registry reports that method for the primary comparison.

The endpoint is relevant to the study question because it counts exacerbations meeting defined treatment or healthcare-use criteria. It does not, by itself, describe every aspect of asthma control, symptoms, lung function or quality of life; those topics appear among the secondary outcomes.

7. Results Posted in the Registry

• GSK3511294: mean 0.46 versus 1.11 on control; difference -0.65 (95% CI -0.96 to -0.34), standardized effect d = -0.53; 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 St. George's Respiratory Questionnaire (SGRQ) Total Score at Week 52

• 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:
  • GSK3511294: mean -13.03 versus -9.67 on control; difference -3.36 (95% CI -7.09 to 0.37), standardized effect d = -0.19; z-test p = 0.077.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GSK3511294 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Asthma Control Questionnaire-5 (ACQ-5) Score at Week 52

• 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:
  • GSK3511294: mean -0.82 versus -0.77 on control; difference -0.05 (95% CI -0.27 to 0.17), standardized effect d = -0.05; z-test p = 0.656.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GSK3511294 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Pre-Bronchodilator Forced Expiratory Volume in One Second (FEV1) At Week 52

• 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:
  • GSK3511294: mean 0.16 versus 0.16 on control; difference 0.00 (95% CI -0.09 to 0.09), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GSK3511294 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address several dimensions beyond the primary exacerbation rate: respiratory health status, asthma control, lung function, nighttime and daily symptoms, and exacerbations involving hospitalization and/or emergency department visits. The registry lists seven outcome measures and six analyses, but detailed results are posted for only some secondary outcomes. The overall pattern among the reported continuous outcomes is that the registry-reported confidence intervals include zero and the individual p-values do not indicate a statistically distinguishable difference at conventional thresholds. The remaining listed secondary outcomes should not be assigned a result from the information in the registry record.

These measures complement rather than replace the primary endpoint. The primary outcome counts clinically significant exacerbations under a specified definition; patient-reported scores, lung function and diary measures assess different aspects of the study. Similarity or difference across these measures need not be expected, because they have distinct scales, measurement processes and statistical properties. A result on the primary endpoint does not establish a corresponding effect on every secondary outcome.

General statistical context: when multiple outcomes are tested, the chance of at least one apparently notable result can increase if each is judged independently without adjustment. Multiplicity methods can control error across a defined family of tests, but the registry does not report whether such a procedure was used or how any testing hierarchy was set. Consequently, individual secondary p-values should be interpreted cautiously and are less persuasive as stand-alone confirmatory evidence than a prespecified primary analysis. The registry’s multiplicity plan is not reported in the registry record.

The secondary findings are therefore best read as additional descriptive evidence about different outcome domains, with uncertainty attached, rather than as a collection of independent conclusions. Missing results for listed outcomes and unreported analysis details further limit the conclusions that can be drawn from the secondary set.

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

• Change From Baseline in St. George's Respiratory Questionnaire (SGRQ) Total Score at Week 52
• Change From Baseline in Asthma Control Questionnaire-5 (ACQ-5) Score at Week 52
• Change From Baseline in Pre-Bronchodilator Forced Expiratory Volume in One Second (FEV1) At Week 52
• Change From Baseline in Asthma Nighttime Symptom Diary (ANSD) Weekly Mean Score at Week 52
• Change From Baseline in Asthma Daily Symptom Diary (ADSD) Weekly Mean Score at Week 52
• Annualized Rate of Exacerbations Requiring Hospitalization and/or Emergency Department (ED) Visit up to 52 Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

The registry’s primary analysis used a negative binomial distribution and reported a rate ratio with a 95% confidence interval and p-value. This is the method and contrast to use when describing the registry’s primary result. It is different from comparing two continuous means, even though the posted calculations also include a simple unadjusted mean difference based on arm-level summary statistics.

What does a rate ratio represent?

A rate ratio compares event rates between groups. A value of 1 represents equal rates; a value below 1 represents a lower rate in the first group named in the comparison relative to the reference group, while a value above 1 represents a higher rate. The posted rate ratio of 0.42 compares the GSK3511294 group with placebo. Its confidence interval gives a range of values compatible with the model and data under the stated confidence procedure. The registry reports the rate ratio as 0.42, the interval as 0.30 to 0.59, and p < 0.001.

General statistical context: event counts often vary more between participants than a simple Poisson model assumes. This is over-dispersion. A negative binomial model can accommodate greater variability in counts and is commonly used for recurrent event-rate data. The registry names the negative binomial distribution, but further details of model specification, covariates, treatment of exposure time and any other adjustments are not reported in the registry record. Those details should not be inferred from the method name alone.

What do the arm estimates and recalculated difference mean?

The posted primary arm estimates are annualized rates: 1.11 in the placebo group and 0.46 in the GSK3511294 group. The posted recalculation also gives a mean difference of -0.65. That difference is an unadjusted subtraction of arm-level rate summaries, whereas the registry-reported primary analysis estimates a rate ratio using a negative binomial model. The two contrasts use different scales and do not have to produce identical numerical summaries or p-values. The registry-reported model is the primary analysis and should lead interpretation of the primary endpoint.

The recalculation uses the posted summary values and approximate standard deviations. It does not reproduce participant-level modeling, adjustment, or any other model features that are not available in the summary data. Its unadjusted p-value is p < 0.001. Because this is a separate, simple calculation, it is best treated as a supplementary description rather than as a second primary analysis.

How are continuous outcomes analyzed?

For the posted secondary outcomes, the registry reports mixed models for repeated measures (MMRM), with differences in least squares means, 95% confidence intervals and p-values. A least squares mean is a model-based group estimate. MMRM is a general approach for analyzing repeated measurements over time, using the available measurements within a model. General statistical context: such models can represent correlations among repeated measurements from the same participant. The registry record does not report the full model specification, the covariance structure, covariates, missing-data assumptions or the exact population definition for each secondary analysis.

The registry lists change from baseline at Week 52 for the St. George’s Respiratory Questionnaire total score, the Asthma Control Questionnaire-5 score and pre-bronchodilator FEV1. It also lists weekly mean scores from symptom diaries and the annualized rate of exacerbations requiring hospitalization and/or an emergency department visit. However, detailed posted results in the record cover only some of those outcomes. Unreported results should not be inferred from the outcomes’ names or from the primary result.

General statistical context: a confidence interval gives a range of estimates compatible with the observed data and specified model, subject to its assumptions. A p-value describes how surprising data at least as incompatible with the null would be if the null and model assumptions held; it is not the probability that a treatment effect is true. Neither statistic conveys all aspects of clinical importance or study conduct.

How should significance tests be read?

The primary analysis reports p < 0.001. For the posted secondary outcomes, the registry gives individual p-values for the analyses it reports. These are not evidence that the entire family of outcomes has been adjusted for multiple testing. The multiplicity plan is not reported in the registry record, so the listed secondary p-values should be read as individual analysis results rather than as confirmatory family-wise tests.

The analysis population description for the primary endpoint says that the FAS included randomized participants who received at least one dose, excluding participants from 1 site with a GCP violation, and that participants were analyzed according to their randomized intervention. The description is the registry’s stated population definition; further details about exclusions, missing observations and sensitivity analyses are not reported in the registry record.

11. Confidence Intervals and Precision

The primary rate ratio was 0.42, with a 95% confidence interval from 0.30 to 0.59. The interval is entirely below 1, the equal-rate reference for a ratio, and the reported p-value is p < 0.001. The confidence interval indicates that the analysis is more compatible with a range of rate ratios than with a single exact value. It does not mean there is a 95% probability that the true rate ratio lies in this particular interval.

General statistical context: confidence intervals express uncertainty under the model and its assumptions. A narrower interval indicates greater precision on the scale being estimated; a wider interval indicates less precision. The interval does not account for every possible limitation, such as bias from study conduct or unreported model choices. Its interpretation depends on the analysis and population to which it applies.

The arm-level primary estimates also have reported 95% confidence intervals: 0.86 to 1.43 for placebo and 0.36 to 0.58 for GSK3511294. These arm intervals describe uncertainty in each estimated annualized rate. They are not a substitute for the confidence interval around the rate ratio, which directly describes the between-group comparison.

For the reported secondary analyses, the confidence intervals vary in relation to their corresponding null contrasts. The St. George’s Respiratory Questionnaire estimate has a 95% interval from -7.11 to 0.39; the Asthma Control Questionnaire-5 estimate has an interval from -0.27 to 0.18; and the pre-bronchodilator FEV1 estimate has an interval from -0.089 to 0.088. Each interval includes zero for the reported difference in least squares means. These ranges convey uncertainty and do not, alone, establish whether any difference is important in practice. Interpretation also depends on the outcome scale and the analysis plan, details of which are not fully reported in the registry record.

The registry’s primary confidence interval belongs to the negative binomial rate-ratio analysis, while the recalculated mean difference is a separate unadjusted contrast. Precision should be judged on the scale of the estimate being discussed, not by treating those different summaries as interchangeable.

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 trial’s original design calculations. For the continuous-outcome illustrations, the figures are participants per arm. They are not total event counts. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for planning is the stated fraction of the observed effect. The rows represent planning for 100%, 75% or 50% of the observed effect. The columns for 80% and 90% power give the number of participants per arm that the illustration estimates would be needed to detect the selected effect at the stated power, under those assumptions.

General statistical context: power is the chance that a specified analysis will reject its null hypothesis if a particular effect is present, under the planning assumptions. The 90% column represents a higher target chance of detection than the 80% column, and generally requires more participants for the same effect. A smaller effect is harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants. The illustrations are based on a continuous-outcome calculation and should not be read as the trial’s original calculation for its negative binomial primary endpoint.

These figures are not observed power. They are forward-looking planning scenarios calculated from the observed effect and stated assumptions, and do not reveal the probability that the study’s result is correct. They also do not replace a design justification based on a prespecified clinically meaningful effect, outcome distribution, allocation, follow-up and analysis plan.

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 = -0.650; pooled standard deviation σ = 1.216.
2. n = 2 × (1.96 + 0.842)² × 1.216² / -0.650² = 54.9, rounded up to 55 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 <- -0.65                      # observed difference in means
sigma <- 1.21570273120998                     # 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(4719832)
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 = 55 (80% power), 74 (90% power)
 75% of observed effect: n per arm = 98 (80% power), 131 (90% power)
 50% of observed effect: n per arm = 220 (80% power), 295 (90% power)
power.t.test: 55.9 
Simulated power at n = 55 per arm: 0.794 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry-reported primary analysis used a negative binomial distribution and estimated a rate ratio of 0.42, with a 95% confidence interval from 0.30 to 0.59 and p < 0.001. That is the analysis aligned with the primary recurrent-event endpoint and should be the main statistical result used in interpretation.

A separate unadjusted recalculation from the posted arm summaries gives a mean difference of -0.65 and p < 0.001. This is a straightforward comparison of summary rates, not a reconstruction of the negative binomial model. It does not account for any model features that cannot be recovered from the posted summary statistics. The difference in scale matters: a mean difference and a rate ratio are not the same estimand.

For the secondary continuous outcomes, the registry-reported MMRM results should likewise be distinguished from recalculated unadjusted differences. For example, the registry-reported SGRQ difference is -3.36 with p = 0.080, while the simple unadjusted calculation gives a difference of -3.36 with p = 0.077. For ACQ-5, the registry-reported difference is -0.04 with p = 0.690, while the unadjusted calculation gives -0.05 with p = 0.656. For FEV1, the registry-reported difference is -0.001 with p = 0.991. These differences reflect distinct analysis approaches and rounding; the recalculations do not supersede the registry-reported analyses. The registry record does not identify an inconsistency that would require treating a recalculation as a correction to the reported results.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and several secondary outcomes, and it reports six analyses across seven outcome measures. A primary outcome gives the study a central comparison, but the existence of several analyses raises the general issue of multiplicity: repeated testing can increase the chance of at least one result appearing statistically notable even when no corresponding effect exists.

General statistical context: multiplicity can be handled through a prespecified hierarchy, adjustment procedure or other strategy that defines how evidence across outcomes will be judged. The registry does not report a multiplicity adjustment, testing hierarchy or other strategy for controlling error across the secondary outcomes. The individual secondary p-values therefore should not be treated as if they were necessarily adjusted or as proof of independent confirmatory findings. The original statistical analysis plan is not reported in the registry record.

The primary population is described as the FAS: randomized participants who received at least one dose, excluding participants from 1 site with a GCP violation. The record says participants were analyzed according to their randomized intervention. This clarifies the stated primary analysis population but does not provide a complete account of all participant flow, exclusions, or analysis populations for each outcome.

Missing-data handling is not reported in the registry record. For the MMRM secondary analyses, the registry names the method but does not provide the assumptions about missing observations, model specification or sensitivity analyses. General statistical context: conclusions from repeated-measures models can depend on assumptions about why measurements are missing and on whether the model is adequately specified. Without those details, the robustness of the secondary analyses to missing data cannot be assessed from the registry record alone.

The registry also does not report the trial’s original sample-size justification, interim-analysis plan or complete statistical plan. None of these details can be inferred from the posted results or the planning illustrations. These gaps limit assessment of how the study’s analysis choices were prespecified and how the full family of outcomes was intended to be interpreted.

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: asthma (3.8%), pneumonia (2.3%), covid-19 (1.5%), arrhythmia (0.8%), colitis (0.8%).

The safety record lists serious adverse events for 22 of 132 participants at risk in the placebo group and 15 of 250 participants at risk in the GSK3511294 group. It lists zero deaths in both groups. The most frequently listed serious adverse-event terms are asthma (3.8%), pneumonia (2.3%), COVID-19 (1.5%), arrhythmia (0.8%), colitis (0.8%) and pancreatitis (0.8%). These percentages are reported terms in the registry record and should not be combined or interpreted as mutually exclusive categories.

The record also lists other adverse events affecting 78 of 132 participants in the placebo group and 145 of 250 in the GSK3511294 group. These are counts for a separate category from serious adverse events. The safety denominators differ from the primary efficacy analysis counts, which are 132 and 249; the analysis-specific counts should be kept distinct.

General statistical context: adverse-event counts describe events observed during a study, not necessarily events caused by the assigned intervention. Comparing safety requires context about event definitions, observation time, severity, baseline risk and the full set of recorded events. The posted figures do not by themselves establish causation or provide a complete account of safety.

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

The primary analysis reports a lower annualized rate estimate in the GSK3511294 group than in the placebo group, with a rate ratio of 0.42 and a 95% confidence interval from 0.30 to 0.59. The reported p-value is p < 0.001. In statistical terms, the result is inconsistent with equal rates under the reported negative binomial analysis and its assumptions. This statement describes the registry-reported comparison; it is not medical advice and does not establish what an individual participant should do.

The result does not mean that every participant had fewer exacerbations, nor does an annualized group rate describe each person’s experience. It does not establish that every asthma-related outcome changed in the same way. The posted secondary analyses address other outcome domains and have their own estimates and uncertainty; the registry record does not report detailed results for every listed secondary outcome.

General statistical context: statistical evidence and clinical importance are related but distinct. A p-value concerns compatibility with a null statistical model, while a confidence interval describes uncertainty in the estimated effect. Neither alone determines whether an effect is important to participants. The registry record does not provide a threshold for a clinically important change in the primary rate or for each secondary measure.

The study compared depemokimab with placebo as adjunctive treatment while participants continued baseline maintenance asthma standard-of-care treatment. Accordingly, the result pertains to that study comparison and population, not to all possible treatment settings or all people with asthma. The record’s stated primary population excludes participants from 1 site because of a GCP violation, and the primary analysis counts differ from the safety counts. These details belong in any interpretation of what population the posted result describes.

Finally, the registry results do not resolve questions that are not reported, including the full statistical analysis plan, missing-data assumptions, multiplicity handling, original sample-size justification and detailed results for all listed outcomes. Those uncertainties do not erase the reported primary result, but they define limits on how broadly the record can support conclusions.

18. Why This Trial Matters Statistically

This study illustrates why the choice of statistical scale should match the outcome. The primary endpoint is a recurrent event rate, and the registry reports a negative binomial analysis as a rate ratio. A simple difference between arm-level rates is also available as a recalculation, but it is a different summary and should not be mistaken for the primary modeled contrast. Keeping those estimands separate prevents a straightforward summary calculation from being presented as if it reproduced the trial’s primary model.

The result also illustrates the role of uncertainty. The rate ratio is accompanied by a 95% confidence interval that remains below the equal-rate reference value, while secondary continuous-outcome intervals include zero. Reporting both estimates and their intervals gives more information than relying on a significance label alone. The interval still depends on the model and does not address unreported design or analysis decisions.

Another statistical lesson is that outcome families matter. This registry contains a primary endpoint and multiple secondary measures covering different domains. A clear primary result can coexist with less conclusive secondary analyses, and the primary finding should not be generalized to every listed outcome. Without a reported multiplicity plan, individual secondary p-values carry less confirmatory weight.

Finally, planning illustrations based on an observed effect are not the same as a prospective sample-size justification. Their assumptions are stated, but the original trial-design assumptions are not reported in the registry record. Distinguishing planning scenarios from observed power, and registry-reported models from summary-statistic recalculations, is essential for a statistically careful reading.

19. Limitations

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

The registry record does not report the original sample-size justification, allocation ratio, interim-analysis plan or full statistical analysis plan. It also does not give the complete primary model specification, including any covariates or exposure-time details. These omissions make it difficult to assess how all analysis choices were prespecified or whether the posted analysis exactly follows the original plan.

The primary population definition excludes participants from 1 site because of a GCP violation, and the efficacy and safety counts differ. The record gives the stated primary population rule but does not provide enough detail to reconstruct participant flow or understand the impact of that site exclusion. The primary analysis population should therefore be kept distinct from the safety population.

Missing-data methods, assumptions and sensitivity analyses are not reported in the registry record. These details are particularly relevant to repeated-measures outcomes, for which the registry names MMRM but does not describe its full specification. The registry also does not report a multiplicity strategy for the collection of secondary outcomes.

Although seven outcome measures and six analyses are listed, detailed results are posted for only some secondary outcomes. This limits evaluation of the full secondary-outcome pattern and makes it inappropriate to infer results for outcomes without posted estimates. The posted secondary analyses should be interpreted as distinct outcome-specific results, not as a complete account of every planned measure.

The sample-size illustrations use fractions of the observed effect and specified planning assumptions; the trial’s original design assumptions are not reported. Those illustrations should not be treated as a retrospective explanation of the actual enrollment or as evidence of observed power. Finally, adverse-event counts describe events recorded in the study and do not by themselves establish causality.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Placebo-controlled Efficacy and Safety Study of GSK3511294 (Depemokimab) in Participants With Severe Asthma With an Eosinophilic Phenotype — NCT04719832.
• Registry record last updated 2024-12-17; status last verified 2024-11.
• Results first posted 2024-12-17.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed Phase 3, randomized, double-blind, placebo-controlled, parallel-group study of depemokimab in adults and adolescents with severe uncontrolled asthma with an eosinophilic phenotype. Enrollment was 395, and the study ran for 52 weeks. Both groups continued baseline maintenance asthma standard-of-care treatment while receiving assigned injections at week 0 and week 26.

The primary endpoint was the annualized rate of clinically significant exacerbations through Week 52. The registry-reported negative binomial analysis gave a rate ratio of 0.42, a 95% confidence interval from 0.30 to 0.59 and p < 0.001. The record also lists secondary outcomes and safety findings, with detailed results available for some but not all listed measures.

The record does not report the original sample-size justification, full statistical analysis plan, missing-data assumptions or multiplicity strategy. These limitations qualify interpretation of secondary results and the completeness of the statistical record.