Study to Assess the Efficacy and Safety of CJM112 in Patients With Inadequately Controlled Severe Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess the Efficacy and Safety of CJM112 in Patients With Inadequately Controlled Severe Asthma (NCT03299686), a randomized phase 2 study. The primary outcome is Change From Baseline in Forced Expiratory Volume in One Second (FEV1).

2. Clinical Question

This is an efficacy question about a measured lung-function outcome over the stated follow-up, not a general question about all asthma symptoms, all patients with asthma, or longer-term outcomes. The study also included patient-reported asthma-control measures and safety outcomes, but those do not replace the prespecified primary question. The registry record does not report enough detail to establish how broadly the enrolled participants represent other asthma populations.

3. Trial Design

This was a phase 2, randomized, parallel-group, placebo-controlled study of CJM112 in inadequately controlled moderate to severe asthma. The registry lists an enrollment of 118 and identifies Novartis Pharmaceuticals as the sponsor. The study status is completed. Its recorded start date is 2017-11-06, and its primary completion date is 2019-04-08.

The registry describes masking as quadruple and the study title as subject- and investigator-blinded. The parallel model means that participants were assigned to a treatment group and followed in that group, rather than each participant receiving both treatments in sequence. The posted comparison is CJM112 300 mg versus placebo. The official title describes a multiple-dose study, but the specific dosing schedule and the allocation ratio are not reported in the registry record.

The primary endpoint was change from baseline in FEV1 in liters at Day 92. The primary analysis population was the Pharmacodynamics analysis set with evaluable FEV1 data at both timepoints. The number of participants in that analysis differs from the overall enrollment: the arm summaries list 53 for CJM112 300 mg and 36 for placebo. These are the posted analysis counts, and the registry record does not explain the difference between those counts and overall enrollment.

Secondary outcomes included change in FEV1 percent predicted, change in ACQ6 and ACQ7 scores, the percentage of participants with at least 0.5 decrease in ACQ7, and adverse events leading to discontinuation. Five secondary outcomes are posted. Reasons that other listed outcome measures do not have posted results are not reported in the registry record. The protocol’s sample-size justification, planned interim analyses, and detailed statistical analysis plan are also 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: After an initial screening visit, run-in period and baseline assessments, the eligible subjects entered the treatment period and were randomized in a 3:2 ratio to one of the two treatment groups.

Treatment Epoch

Reasons for not completing this period:

Follow-up Epoch

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis population included the Pharmacodynamics (PD) analysis set with evaluable FEV1 data at both timepoints.

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 Forced Expiratory Volume in One Second (FEV1), measured over Baseline, Day 92.

The primary endpoint is the absolute change from baseline in trough forced expiratory volume in one second (FEV1), measured in liters, at Day 92. FEV1 is the volume of air a person can forcibly exhale in one second, measured by spirometry. The registry defines baseline using the pre-bronchodilator spirometry assessment at the baseline visit. The endpoint therefore captures a change in a specific, instrument-measured aspect of lung function over the stated study period.

Comparing average change between randomized groups asks whether the observed shift differs between participants assigned to CJM112 and those assigned to placebo. Randomization supports a between-group comparison by allocating participants to groups, while placebo provides a comparison under the study’s masked conditions. The result remains specific to this endpoint, the analyzed population, and the timing specified in the registry; it is not itself a complete account of asthma control, symptoms, safety, or outcomes beyond Day 92.

In general, a continuous endpoint such as FEV1 retains information about the magnitude of each participant’s measured value, and group means provide a concise description of average change. Variation between participants matters because the same mean difference can be estimated with different precision depending on the amount of variability and the number of observations. The primary analysis population required evaluable measurements at baseline and Day 92, so its estimates pertain to participants included in that analysis rather than automatically to every person enrolled.

7. Results Posted in the Registry

• CJM112 300 mg: mean 0.04 versus 0.02 on control; difference 0.03 (95% CI 0.01 to 0.04), standardized effect d = 0.88; 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 Forced Expiratory Volume 1 (FEV1) % of Predicted

• 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:
  • CJM112 300 mg: mean 1.06 versus 0.15 on control; difference 0.91 (95% CI -1.90 to 3.72), standardized effect d = 0.14; z-test p = 0.524.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CJM112 300 mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Asthma Control Questionnaire 6 (ACQ6) 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:
  • CJM112 300 mg: mean -0.93 versus -0.71 on control; difference -0.22 (95% CI -0.50 to 0.06), standardized effect d = -0.32; z-test p = 0.122.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CJM112 300 mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Asthma Control Questionnaire 7 (ACQ7) 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:
  • CJM112 300 mg: mean -0.83 versus -0.60 on control; difference -0.23 (95% CI -0.48 to 0.02), standardized effect d = -0.39; z-test p = 0.072.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CJM112 300 mg and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover a lung-function measure, two asthma-control scores, a threshold-based ACQ7 response, and adverse events leading to discontinuation. Taken together, the continuous secondary results do not form a uniformly precise pattern: the reported estimates differ in magnitude and their model-based intervals vary in whether they include zero. These outcomes concern distinct measurements and should not be collapsed into a single overall measure of benefit.

The secondary lung-function endpoint, FEV1 percent predicted, relates to the primary FEV1 question but expresses lung function on a different scale. ACQ6 and ACQ7 are asthma-control measures, so they contribute a patient-control perspective rather than duplicating the spirometric endpoint. The threshold outcome further summarizes the proportion meeting a specified change in ACQ7. The registry record lists five posted secondary outcomes, but does not report results for every measure count indicated in the record or explain why.

Secondary findings can add context to the primary result, but they do not reverse or replace it. The primary sponsor analysis has an interval spanning zero and differs sharply in inferential appearance from the simple recalculation. The secondary outcomes also include model-based results that do not always align with recalculated summaries. This combination supports caution in treating any one secondary result as a decisive confirmation of the primary question.

General: when several outcomes are analyzed, unadjusted results carry less weight as confirmatory evidence because repeated testing can raise the chance of finding a seemingly notable result by chance. A multiplicity adjustment or prespecified testing hierarchy can address this issue, but one is not reported in the registry record. The secondary p-values should therefore be interpreted as outcome-specific evidence, with attention to their estimates and intervals, rather than as a set of independent declarations. No explanation for missing secondary results or details of adjustment are reported in the registry record.

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

• Change From Baseline in Forced Expiratory Volume 1 (FEV1) % of Predicted
• Change From Baseline in Asthma Control Questionnaire 6 (ACQ6) Score
• Change From Baseline in Asthma Control Questionnaire 7 (ACQ7) Score
• Percentage of Patients With at Least 0.5 Decrease in ACQ7 Score
• Percentage of Patients With Adverse Events (AEs) Leading to Discontinuation of Study Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

What does a difference in means represent?

For a continuous endpoint, each arm summary reports an average change. The between-arm mean difference expresses how far apart those average changes are, with the direction determined by which arm is subtracted from the other. For the primary FEV1 summaries, the posted arm means are 0.043 liters for CJM112 300 mg and 0.016 liters for placebo; the recalculated difference is 0.027 liters. The difference is an average contrast, not a statement that every participant changed by that amount. Individual responses can vary around the group means.

General: a mean is useful for describing the center of continuous measurements, but it does not show the full distribution. A standard deviation describes variation among observations, whereas a standard error describes uncertainty in an estimated mean. The primary arm summaries report standard deviations of 0.031 and 0.03. Several secondary arm summaries report standard errors instead. These dispersion measures should not be treated as equivalent: they answer different questions and are not directly comparable as descriptions of individual variation.

What does an interval communicate?

General: a confidence or model-based interval shows a range of values compatible with an estimate under the assumptions of the method used. Its width reflects precision: a wider interval leaves more uncertainty about the size and direction of the contrast, while a narrower interval indicates a more concentrated estimate under that method. An interval containing zero does not identify a clear nonzero difference at the interval’s stated level; an interval excluding zero indicates that zero is outside that range. Such statements must be tied to the actual method and interval level.

The sponsor’s primary result is explicitly reported with an 80% interval, from -0.029 to 0.082 liters. The unadjusted recalculation has an interval from 0.014 to 0.040, but its confidence level is not reported in the registry record. Because the levels and methods are not stated as equivalent, those ranges should not be compared as if they were produced by the same analysis. The sponsor’s reported analysis takes precedence where the results conflict.

Why can methods yield different results?

The recalculation is a simple unadjusted comparison based on posted group summaries. It does not reproduce the sponsor’s Bayesian linear repeated measures model. A repeated-measures model can use the structure of measurements over time, whereas a calculation from endpoint summaries cannot incorporate model features that are not represented in those summaries. General: different assumptions, data handling, covariate adjustment, repeated-measure structure, and inferential frameworks can affect uncertainty and p-values. The registry record does not provide enough detail to say which specific feature explains the discrepancy in this trial. It would be inappropriate to select a reason by assumption.

The primary arm counts are 53 and 36 in the summaries, and the primary analysis population requires evaluable FEV1 at both timepoints. The record does not provide participant-level data or a complete account of missing observations. It therefore does not allow reconstruction of the sponsor’s model, assessment of the effects of missing data, or verification of its reported uncertainty from the summary values alone.

How should p-values be understood?

General: a p-value describes how unusual results at least as far from a specified null value would be under a particular statistical model if that null value were true. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of a difference. A p-value also depends on the analysis method and assumptions. Thus p < 0.001 from the unadjusted recalculation and the sponsor’s p = 0.737 are not competing readings of one identical test; they come from different analyses. The sponsor’s reported model result is the trial analysis to prioritize.

The secondary outcomes add further complexity because multiple outcomes were evaluated. General: when many hypotheses are examined, the chance of at least one apparently notable result can increase if the analyses are treated as independent opportunities without an adjustment or a prespecified hierarchy. The registry record does not report a multiplicity strategy. Secondary p-values should therefore be read as exploratory evidence in the context of the other outcomes, rather than as a collection of equally definitive confirmatory tests.

What is known about the analysis plan?

The record identifies the sponsor’s primary method as a Bayesian linear repeated measures model and gives the primary analysis population. It names Mixed Models Analysis for the posted FEV1 percent-predicted, ACQ6, and ACQ7 secondary results. It does not report the detailed model formulas, covariates, prior distributions, missing-data assumptions, multiplicity adjustments, or the original sample-size justification. Those details cannot be inferred from the method labels. The posted information supports an explanation of the reported estimates and their limits, but not a full audit or reproduction of the trial’s statistical analysis.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is a net mean difference of 0.027 liters. Its reported 80% interval ranges from -0.029 to 0.082 liters. Because this range spans zero, it is compatible under the reported model with values on either side of zero. Its width also indicates that the sponsor’s estimate leaves considerable uncertainty about the size and direction of the primary contrast. The reported p-value is 0.737.

The unadjusted recalculation from the posted arm summaries gives the same point estimate, 0.027 liters, but its interval runs from 0.014 to 0.040 and its p-value is < 0.001. The confidence level for that recalculated interval is not reported in the registry record. The difference between the reported inferential results is therefore not just a difference in wording: the two analyses give notably different accounts of uncertainty. Since the sponsor’s own analysis takes precedence, the narrower recalculated interval should not be used to override the model-based primary result.

General: precision is about how tightly an analysis estimates a quantity, not whether the result is important or whether a treatment should be used. Intervals are interpretable only in relation to their method and stated level. The 80% level is identified for the sponsor’s reported interval; the registry record does not identify the level for the recalculated interval. Comparing interval widths without accounting for those differences can mislead.

The primary summaries include 53 participants in the CJM112 group and 36 in the placebo group, drawn from the specified analysis population. The record does not explain the difference from total enrollment or report the impact of missing measurements. This limits what can be concluded about how sensitive precision is to analysis-population choices. The posted estimates describe the recorded analyses; they do not eliminate uncertainty about model assumptions or unreported aspects of data handling.

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 calculation. For these continuous outcomes, the figures are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row considers detecting the stated fraction of the observed effect. The original protocol’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a design that would have an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding planning count for a higher target chance of detection. These are prospective design illustrations, not guarantees about a future study’s result.

The rows that use 100%, 75%, and 50% of the observed effect illustrate how the planning requirement changes when the target effect is smaller. Under the stated calculation, smaller effects need more participants to detect, because they are harder to distinguish from random variation. The figures are particularly sensitive to the estimated effect used as a planning input. An effect estimated in a small study can itself be uncertain, so the illustration should not be treated as a definitive design recommendation.

These calculations are not observed power. Observed power is not a useful substitute for interpreting the estimate and its uncertainty after results are known. The planning figures do not establish that the trial was adequately or inadequately sized for its original objectives; the trial’s own design justification is not reported in the registry record.

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 = 0.027; pooled standard deviation σ = 0.031.
2. n = 2 × (1.96 + 0.842)² × 0.031² / 0.027² = 20.2, rounded up to 21 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 <- 0.027                      # observed difference in means
sigma <- 0.0306016301872129                     # 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(3299686)
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 = 21 (80% power), 27 (90% power)
 75% of observed effect: n per arm = 36 (80% power), 48 (90% power)
 50% of observed effect: n per arm = 81 (80% power), 108 (90% power)
power.t.test: 21.2 
Simulated power at n = 21 per arm: 0.796 (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 primary analysis is a Bayesian linear repeated measures model with a reported net mean difference of 0.027 liters, an 80% interval from -0.029 to 0.082, and p = 0.737. The recalculation from the posted group summaries also gives a mean difference of 0.027 liters, but its interval is 0.014 to 0.040 and its p-value is < 0.001. Thus the point estimates match, while the reported uncertainty and inferential conclusions differ.

The recalculation is a simple unadjusted calculation from summary statistics. It does not reproduce the sponsor’s repeated-measures model. The registry record does not explain the source of the discrepancy, and the available summary information is not enough to resolve it. The results should not be blended or treated as two equally authoritative versions of the primary analysis: the sponsor’s own analysis takes precedence.

The same caution applies when considering recalculated results for secondary endpoints alongside their reported model-based analyses. The sponsor’s reported analyses are the analyses identified in the registry record, while recalculations are checks based on posted summaries. Differences in methods and uncertainty should remain explicit rather than being attributed to an unreported modeling choice.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary FEV1 outcome and multiple secondary outcomes. It does not report a multiplicity adjustment, a testing hierarchy, or a statement identifying which secondary analyses were intended to be confirmatory. When several outcomes are examined, an unadjusted p-value for an individual outcome does not account for the broader set of comparisons. General: the more opportunities there are to identify an apparently unusual result, the more important it is to know whether and how the analysis plan controlled that risk. Without the plan, secondary results should be interpreted cautiously.

The primary analysis population is described as the Pharmacodynamics analysis set with evaluable FEV1 data at both baseline and Day 92. This defines an important boundary on the reported primary estimate. The record does not state how many enrolled participants lacked evaluable values, why they were not evaluable, or what missing-data method was used in the repeated-measures model. It also does not report sensitivity analyses for missing data. No assumptions about missingness or the likely direction of any resulting bias can be justified from the registry information.

Overall enrollment is 118, while the primary arm summaries list 53 for CJM112 300 mg and 36 for placebo. The registry record does not explain the difference, and these counts should not be taken as a complete accounting of participant flow. Some secondary summaries have different arm counts, also without a detailed explanation in the record. It is therefore not possible to determine from these summary entries alone whether the populations differed because of endpoint availability, analysis rules, or another reason.

The record names Bayesian linear repeated measures modeling for the primary analysis and Mixed Models Analysis for several secondary outcomes, but does not give full model specifications. It does not report the original sample-size justification, interim analyses, multiplicity procedures, or detailed statistical plan. These omissions limit assessment of prespecification, analytic sensitivity, and the relationship between planned and reported analyses. They do not prove that a procedure was absent; they mean its details are not reported in the registry record.

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: stress cardiomyopathy (2.1%), pneumonia (2.1%), asthenia (1.4%), urinary tract infection (1.4%), depression (1.4%).

The safety summaries report serious adverse events for 3 of 70 participants at risk in the CJM112 300 mg group and 2 of 48 at risk in the placebo group. The record also lists other adverse events for 55 of 70 and 38 of 48 participants, respectively. These are counts among the stated at-risk groups; they are not the same denominators as the primary efficacy analysis counts. The registry reports zero deaths in both groups.

The listed serious-event terms include stress cardiomyopathy and pneumonia, each reported as 2.1%, and asthenia, urinary tract infection, depression, and asthmatic crisis, each reported as 1.4%. Those entries describe the registry’s reported terms and percentages; they do not provide a complete account of severity, timing, duration, recurrence, or attribution for each event. The record does not report whether events were considered related to study treatment.

These safety counts are descriptive. They should be read with the group sizes and follow-up context in mind, and do not by themselves establish whether a treatment caused an event or how risks compare beyond this study. The registry record does not report additional detail needed to assess those questions.

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

The primary result is an estimate of the difference in mean FEV1 change between the CJM112 300 mg and placebo groups at Day 92, in the specified analysis population. The sponsor’s reported estimate is 0.027 liters, with an 80% interval from -0.029 to 0.082 and p = 0.737. This interval includes zero and leaves uncertainty about both the direction and magnitude of the between-group difference under the reported model.

A simple unadjusted recalculation from the posted summaries gives the same point estimate but a different interval and p-value. Because that conflicts with the sponsor’s analysis, the sponsor’s own analysis takes precedence. The discrepancy is a reason to distinguish the two methods, not a basis to choose whichever result appears more favorable. The registry record does not explain the discrepancy or supply enough detail to resolve it independently.

The result does not establish that the treatment does or does not work. It describes one measured outcome over a defined period in a particular analysis set. It does not establish effects on every asthma symptom, long-term outcomes, or populations beyond the studied participants. The secondary outcomes provide additional but not definitive context, especially because the registry does not report a multiplicity approach and the analyses do not all give the same inferential picture.

Safety counts show serious adverse events in both groups and zero reported deaths in either group. The counts alone cannot establish causation, quantify all possible safety differences, or predict what would happen outside this study. The study record is not a substitute for a complete assessment of an individual’s circumstances, and no treatment decision follows from these registry summaries alone.

18. Why This Trial Matters Statistically

This trial illustrates why a reported point estimate cannot be interpreted without its analysis method and uncertainty. The sponsor and the simple recalculation yield the same primary mean difference, 0.027 liters, yet give markedly different intervals and p-values. The difference makes clear that arithmetic agreement on an estimate does not guarantee agreement about how precisely it is known. A reader needs to distinguish the sponsor’s repeated-measures analysis from a calculation based only on arm summaries.

It also highlights the role of the analysis population. The primary result applies to the Pharmacodynamics analysis set with evaluable FEV1 measurements at both timepoints, while the registry reports overall enrollment separately. The record does not explain the difference in counts. Transparent reporting of participant flow, missing-data handling, model specifications, and analysis populations would help readers understand how trial results were obtained and how robust they may be.

Finally, the study includes multiple secondary outcomes across lung function, asthma control, and safety. Each provides a different kind of information, but multiple outcomes complicate interpretation when no multiplicity approach is reported. The example reinforces a general statistical principle: estimates, uncertainty, analysis populations, and the planned testing strategy all matter. A single p-value or a single endpoint cannot capture the full evidentiary picture.

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 primary model-based result and the simple unadjusted recalculation disagree in their reported uncertainty and p-values. The sponsor’s result takes precedence, but the registry record does not provide enough model detail to reproduce it or explain the discrepancy. The comparison therefore depends on accepting a reported analysis whose implementation is not fully described in the record.

The primary analysis includes participants with evaluable FEV1 at both timepoints, and its arm counts are smaller than overall enrollment. The registry does not explain the difference, report a complete participant flow, or describe the handling of missing observations. The posted summaries cannot show whether those with missing values differed from those analyzed.

The study was phase 2 and enrolled 118 participants overall. The record does not report the original sample-size rationale or the intended precision for the primary endpoint. A planning illustration based on the observed effect cannot substitute for the trial’s design justification. The follow-up specified for the primary outcome is baseline to Day 92; the record does not establish longer-term outcomes.

Five secondary outcomes have posted results, and the record does not explain the absence of results for all listed outcome measures. It also does not report a multiplicity adjustment or testing hierarchy. Secondary findings should therefore be viewed as context rather than definitive confirmation. The study description focuses on people with low IgE and low circulating eosinophil levels, so the results should not automatically be generalized to all people with asthma. Details about dosing schedule and broader participant characteristics are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Assess the Efficacy and Safety of CJM112 in Patients With Inadequately Controlled Severe Asthma — NCT03299686.
• Registry record last updated 2021-10-08; status last verified 2021-10.
• Results first posted 2020-08-06.
• 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

NCT03299686 is a completed phase 2 randomized, quadruple-masked, parallel, placebo-controlled study of CJM112 300 mg in inadequately controlled moderate to severe asthma. Overall enrollment was 118. The primary endpoint was change in trough FEV1 from baseline to Day 92, analyzed in the Pharmacodynamics set with evaluable measurements at both timepoints.

The sponsor reported a Bayesian linear repeated measures estimate of 0.027 liters, with an 80% interval from -0.029 to 0.082 and p = 0.737. A recalculation from posted summaries has the same point estimate but different uncertainty and p-value; the sponsor’s own analysis takes precedence. Secondary lung-function and asthma-control outcomes offer additional context, while multiplicity procedures, detailed missing-data methods, and the original sample-size justification are not reported in the registry record. Safety summaries report serious adverse events in both groups and zero deaths in either group.