Study of Efficacy and Safety of CSJ117 in Patients With Severe Uncontrolled Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Efficacy and Safety of CSJ117 in Patients With Severe Uncontrolled Asthma (NCT04410523), a randomized phase 2 study. The primary outcome is Average Change From Baseline in Pre-dose FEV1 at Week 8 and Week 12.

2. Clinical Question

FEV1 is a spirometry measure of the volume of air forcibly exhaled in the first second of a forced exhalation. The endpoint is expressed in liters, and the registry record treats a positive change from baseline as favorable. It averages the pre-dose measurements at the Week 8 and Week 12 visits, rather than asking only whether participants improved at a single visit.

The study was registered as a phase 2 trial in adults with severe uncontrolled asthma. Its purpose was to assess efficacy and safety for multiple CSJ117 doses compared with placebo when added to existing asthma therapy. The registry record reports five active dose groups and one placebo group. It does not state a minimum clinically important difference for FEV1, so the clinical importance of any numerical difference cannot be determined from the posted results alone.

3. Trial Design

This was a randomized, multicenter, double-blind, parallel-arm, placebo-controlled study. The registry record identifies quadruple masking, meaning the masking designation covered multiple trial roles; it does not describe which roles were masked or how masking was maintained. The recorded enrollment was 335. The trial was listed as phase 2 and its status is terminated. The reason for termination is not reported in the registry record.

Participants received once-daily inhaled CSJ117 at 0.5 mg, 1 mg, 2 mg, 4 mg, or 8 mg, or once-daily inhaled placebo. All groups continued standard-of-care asthma therapy. The official study description specifies a 12-week treatment period. The primary endpoint averages pre-dose FEV1 change from baseline across the Week 8 and Week 12 visits. The registry also lists secondary measures of airway inflammation, peak expiratory flow, asthma control, quality of life, symptom diaries, and short-acting bronchodilator use.

The primary population was the Full Analysis Set: participants assigned double-blind treatment who received at least one dose. The arm-level primary results include 36 participants in the 0.5 mg group, 37 in the 1 mg group, 37 in the 2 mg group, 76 in the 4 mg group, 74 in the 8 mg group, and 75 in the placebo group. These are the reported analysis counts for this endpoint; they should not be read as the count in every analysis or as proof that every enrolled participant completed follow-up.

The registry record does not report the trial’s original sample-size justification, planned allocation ratio, detailed randomization procedures, or reasons for stopping the study. It also does not provide a narrative explanation of the termination status. These omissions limit what can be concluded about the study’s original design rationale and conduct beyond the recorded design features.

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: The screening period of approximately 2 weeks began after the participants had provided written informed consent. There was a single blinded placebo run-in period of 4 weeks (extended to 8 weeks for subjects experiencing an asthma exacerbation or respiratory tract infection during the run-in period) before starting the double blinded treatment period.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS). The FAS included all participants to whom double-blind treatment had been assigned and who received at least one dose of double-blind treatment.

5. Baseline Characteristics

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

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Average Change From Baseline in Pre-dose FEV1 at Week 8 and Week 12, measured over Baseline, Weeks 8-12.

The primary endpoint is average change from baseline in pre-dose FEV1 at Week 8 and Week 12, measured in liters. FEV1, or forced expiratory volume in one second, is the amount of air a person can forcibly exhale during the first second of a forced exhalation. It is measured with spirometry. For the endpoint, pre-dose FEV1 is the average of two measurements taken shortly before dosing at each visit. Baseline is defined using two measurements before the first dose of double-blind treatment.

Change from baseline expresses the later measurement relative to that participant’s baseline value. Averaging across the two follow-up visits produces a measure that reflects the treatment-period response at both scheduled assessments, rather than relying on a single visit. The registry describes the reported group estimates as least-squares means obtained from a linear mixed-effects model for repeated measures. The stated direction is that a positive average change is favorable.

FEV1 is used as a continuous measure of lung function, so the reported estimates retain the measurement unit and allow the magnitude of change to be considered. However, a statistical difference alone does not establish how important that difference is to participants. The registry record does not state a threshold for a clinically meaningful change, nor does it provide enough information to judge the relationship between this endpoint and longer-term outcomes.

7. Results Posted in the Registry

• CSJ117 0.5mg: mean 0.17 versus 0.05 on control; difference 0.12 (95% CI 0.02 to 0.23), standardized effect d = 0.46; z-test p = 0.024.
• CSJ117 1mg: mean 0.11 versus 0.05 on control; difference 0.06 (95% CI -0.05 to 0.16), standardized effect d = 0.22; z-test p = 0.285.
• CSJ117 2mg: mean 0.12 versus 0.05 on control; difference 0.07 (95% CI -0.04 to 0.17), standardized effect d = 0.25; z-test p = 0.212.
• CSJ117 4mg: mean 0.06 versus 0.05 on control; difference 0.01 (95% CI -0.08 to 0.09), standardized effect d = 0.03; z-test p = 0.834.

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.

Average Change From Baseline in FeNO at Week 8 and Week 12

• 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:
  • CSJ117 0.5mg: mean -2.87 versus -1.30 on control; difference -1.57 (95% CI -6.20 to 3.07), standardized effect d = -0.14; z-test p = 0.507.
  • CSJ117 1mg: mean -5.30 versus -1.30 on control; difference -4.00 (95% CI -8.67 to 0.67), standardized effect d = -0.34; z-test p = 0.093.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CSJ117 0.5mg 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 CSJ117 1mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Morning PEF at Week 12

• 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 deviations.
• Result:
  • CSJ117 0.5mg: mean -0.98 versus -2.21 on control; difference 1.23 (95% CI -8.87 to 11.33), standardized effect d = 0.05; z-test p = 0.812.
  • CSJ117 1mg: mean -1.70 versus -2.21 on control; difference 0.50 (95% CI -11.11 to 12.11), standardized effect d = 0.02; z-test p = 0.932.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CSJ117 0.5mg 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 CSJ117 1mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Evening PEF at Week 12

• 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 deviations.
• Result:
  • CSJ117 0.5mg: mean -5.39 versus -3.28 on control; difference -2.11 (95% CI -14.25 to 10.03), standardized effect d = -0.08; z-test p = 0.733.
  • CSJ117 1mg: mean -7.87 versus -3.28 on control; difference -4.59 (95% CI -16.55 to 7.37), standardized effect d = -0.18; z-test p = 0.452.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CSJ117 0.5mg 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 CSJ117 1mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering FeNO, morning and evening peak expiratory flow, asthma control, asthma-related quality of life, symptom diary scores, and daily short-acting bronchodilator puffs. The overall secondary pattern is not a uniform movement across all measures or doses. The posted numerical summaries include both positive and negative changes, and the sizes of the estimates vary by outcome and group. The results therefore provide additional descriptive context rather than a single consistent signal that can be read as confirming the primary result.

Some secondary measures address related but distinct aspects of asthma. FeNO is an inflammatory marker, while peak expiratory flow is a measure of airflow and the questionnaire or diary outcomes capture reported symptoms, control, or quality of life. A result on one measure does not automatically establish a corresponding result on another. Nor does a secondary measure replace the primary endpoint, which was average change in pre-dose FEV1 at Week 8 and Week 12.

Secondary findings generally carry less weight when many outcomes, visits, and dose comparisons are examined. In general, multiple statistical tests increase the chance of observing an apparently notable result by chance if no adjustment or prespecified testing hierarchy is used. The registry record does not report the multiplicity procedure, if any, for secondary outcomes. It also does not describe whether the outcome analyses were intended to support confirmatory claims. Accordingly, the secondary results are best read as exploratory or supportive evidence unless further analysis-plan information establishes otherwise. No conclusion about an overall treatment effect should rest on isolated secondary estimates alone.

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

• Average Change From Baseline in FeNO at Week 8 and Week 12
• Change From Baseline in Morning PEF at Week 12
• Change From Baseline in Evening PEF at Week 12
• Average Change From Baseline in ACQ-5 Score at Week 8 and Week 12
• Average Change From Baseline in AQLQ+12 Score at Week 8 and Week 12
• Change From Baseline in ADSD Score at Week 8 and Week 12
• Change From Baseline in ANSD Score at Week 8 and Week 12
• Change From Baseline in Number of Puffs of SABA Taken Per Day at Week 12

9. Statistical Interpretation

10. Statistical Methods Explained

The primary analysis is described as a linear mixed-effects model for repeated measures, abbreviated MMRM in the registry. This is a general statistical approach for outcomes measured repeatedly over time. It models the pattern of measurements across visits and accounts for the fact that observations from the same participant are related. In this trial, the reported primary measure averages change in pre-dose FEV1 across Week 8 and Week 12. The registry reports least-squares means from the model rather than only raw arithmetic averages.

What does a least-squares mean represent?

In general, a least-squares mean is a model-based estimate of a group mean. It can differ from a simple raw mean because it is estimated within the fitted model. The registry identifies the MMRM method but does not report the model’s full specification, including its covariates, covariance structure, or detailed handling of visits. Those details are not reported in the registry record, so the model cannot be fully reconstructed from the posted information.

How should the comparison be read?

The sponsor’s reported comparison is the estimated difference between a CSJ117 dose group and placebo in average change from baseline. A positive difference favors the direction defined as favorable in the endpoint description. The estimate is paired with a confidence interval and a p-value. The interval describes a range of values compatible with the data and model under repeated sampling; it does not give the probability that the true value lies within that particular interval. A p-value measures how unusual data at least as inconsistent with a specified null hypothesis would be under the assumptions of the statistical test. It is not the probability that the null hypothesis is true.

The sponsor’s primary analyses report model-based differences with 95% confidence intervals. The separate recalculations use posted arm-level estimates and standard errors to form simple unadjusted comparisons. These calculations do not reproduce all of the information used by the sponsor’s repeated-measures model. Some reconstructed variability is approximate, and the recalculated intervals and p-values differ slightly from the sponsor’s reported values. Because a discrepancy is flagged, the sponsor’s analysis is the primary reference for interpreting the endpoint; the recalculations are supplementary descriptive checks.

Why does repeated measurement matter?

In general, repeated measurements can improve estimation by using information from more than one follow-up visit and by representing within-participant correlation. They also introduce modeling choices. The assumptions made about the relationship among visits and the treatment of incomplete follow-up can affect estimates and uncertainty. The registry record does not report the covariance structure, the missing-data assumptions, sensitivity analyses, or whether any supplementary models were used. It is therefore not possible to assess how robust the primary results are to alternative choices using this record alone.

What do the re-calculations add?

The posted summary statistics include arm-level least-squares mean changes and standard errors. A simple unadjusted re-calculation compares the active group and placebo using those summaries. It is useful as a check on the direction and rough size of the contrast, but it is not equivalent to fitting the sponsor’s MMRM. The difference in reported intervals or p-values is not evidence by itself that either analysis is erroneous. The sponsor’s analysis reflects the stated repeated-measures method and takes precedence when the results differ.

How should the planning illustrations be understood?

The sample-size illustrations are based on the observed effect and specified planning assumptions. In general, a planning calculation asks how many participants might be needed to detect an effect under an assumed design and statistical model. It does not establish that a trial was adequately powered for its original question, and it does not measure the probability that the observed result is correct. The illustrations are not the trial’s own design justification. The trial’s original sample-size assumptions are not reported in the registry record.

For continuous outcomes, variability matters because a larger spread makes a group difference harder to distinguish from chance variation. General statistical reasoning also cautions that planning estimates based on observed effects may be unstable, particularly when the observed effect is imprecise. The assumptions attached to these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use the stated fraction of the observed effect to be detected. The outcome-specific figures are planning illustrations, not observed results or claims about the trial’s actual statistical power.

What is not specified?

The registry record does not report a full statistical analysis plan, the original sample-size calculation, interim analyses, the primary testing hierarchy, or adjustments for multiple comparisons. It also does not state the exact rules for missing observations or provide sensitivity analyses. These are important elements when evaluating a trial with several doses and repeated measurements. Their absence from the record does not show that the procedures were absent from the trial; it means their details cannot be assessed from the registry information.

11. Confidence Intervals and Precision

A confidence interval communicates precision by pairing an estimated difference with a range of values that are reasonably compatible with the data and the model. A narrow interval indicates more precision than a wide interval, while an interval that includes zero leaves open the possibility of no difference in the measured outcome. The interval is not a guarantee that the true effect falls inside it, and it does not capture every source of uncertainty, such as choices not described in the registry record.

For the sponsor-reported 0.5 mg comparison, the estimated difference is 0.122 L and the 95% confidence interval is 0.016 to 0.229 L. This interval lies above zero, but it still spans a range of positive values. For the 1 mg comparison, the estimate is 0.058 L and the interval is -0.049 to 0.165 L. For 2 mg, the estimate is 0.065 L and the interval is -0.037 to 0.168 L. Both intervals include zero. The 4 mg estimate is 0.009 L, with an interval from -0.076 to 0.094 L, and the 8 mg estimate is -0.008 L, with an interval from -0.094 to 0.077 L. Those intervals also include zero.

The intervals show why the point estimates should not be read in isolation: the estimates for the higher doses are close to zero, but their intervals also allow values on either side of zero. The registry record does not provide a threshold for a clinically important difference, so the confidence intervals cannot be classified as excluding or including effects of clinical importance. The sponsor and recalculated intervals differ slightly; given the flagged discrepancy, the sponsor’s reported intervals are the appropriate primary figures to interpret.

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, each figure is the number of participants per arm, rather than a total number of events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set at the listed fraction of the observed effect.

The 80% power column describes the approximate number of participants per arm under those assumptions for a planning scenario in which the true effect is the selected fraction of the observed effect. The 90% power column uses a higher target probability of detecting that assumed effect if it exists, under the same planning framework. Neither column describes a result that was observed in this trial. These are planning illustrations, not observed power.

Rows planning for 75% or 50% of the observed effect consider smaller effects than the row planning for 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions. The resulting values can become very large when the observed contrast is small. They should not be interpreted as a recommendation for a future study without a separate design assessment, including a justified target effect, appropriate analysis plan, and consideration of the study population and outcome.

The registry record does not report the trial’s own sample-size justification or original planning assumptions. The illustrations therefore cannot establish what enrollment target the investigators used, whether the study achieved its intended power, or whether the decision to terminate was related to sample size or efficacy results.

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 = 0.122; pooled standard deviation σ = 0.267.
2. n = 2 × (1.96 + 0.842)² × 0.267² / 0.122² = 75.4, rounded up to 76 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 <- 0.122                      # observed difference in means
sigma <- 0.267408742900857                     # 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(4410523)
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 = 76 (80% power), 101 (90% power)
 75% of observed effect: n per arm = 135 (80% power), 180 (90% power)
 50% of observed effect: n per arm = 302 (80% power), 404 (90% power)
power.t.test: 76.4 
Simulated power at n = 76 per arm: 0.797 (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 reports the primary comparisons from an MMRM analysis, with least-squares mean differences, 95% confidence intervals, and p-values. The separate recalculations use posted summary statistics for simple, unadjusted comparisons. They are useful for checking the broad scale and direction of the posted results, but they do not reproduce the sponsor’s full repeated-measures analysis.

A discrepancy is flagged between the sponsor’s analyses and the recalculations. For the 0.5 mg comparison, both report an estimated difference of 0.122 L, while the recalculated interval is 0.016 to 0.228 with p = 0.024 and the sponsor reports 0.016 to 0.229 with p = 0.025. Slight differences are also present in the other comparisons. The sponsor’s own analysis takes precedence because it is the reported model-based analysis for the primary endpoint.

The recalculations should not be used to override or “correct” the sponsor’s results. They simplify the analysis and may use approximations to recover variability from summary data. The reported MMRM results are the appropriate figures for describing the sponsor’s primary analysis, while the recalculated values offer a transparent, limited cross-check. Neither set of numbers resolves missing details about the model specification or multiplicity procedures, which are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The study compares five CSJ117 doses with placebo for the primary endpoint and also records numerous secondary outcomes. When several statistical comparisons are made, the chance of at least one apparently unusual result can increase even if all the underlying null hypotheses are true. In general, multiplicity procedures may control this issue by adjusting significance thresholds, ordering tests, or defining a hierarchy in advance. The registry record does not report whether the primary dose comparisons were adjusted, whether a testing hierarchy was prespecified, or how multiplicity was handled for secondary outcomes.

This omission affects interpretation of the reported p-values. The sponsor reports p = 0.025 for the 0.5 mg comparison and larger p-values for the other primary dose comparisons. Without the stated multiplicity plan, the p-values should be read as reported for their individual comparisons, not assumed to establish a family-wide error rate across all doses. The confidence intervals likewise describe the reported comparisons; the record does not state whether they were adjusted for multiple testing.

The analysis population is defined: the Full Analysis Set included participants assigned double-blind treatment who received at least one dose. The registry record does not state how many assigned participants were excluded from this population, provide details of missing outcome measurements, or describe the assumptions used for incomplete follow-up. It does not report sensitivity analyses to assess the effect of missing data. These details are important because repeated-measures estimates can depend on how incomplete observations are handled.

The record also does not report interim analyses, stopping boundaries, or whether the termination decision followed a planned rule. The reason for termination is not reported in the registry record. These omissions do not demonstrate that such procedures were absent, but they prevent an assessment of their potential influence on the statistical results. The primary model is identified as MMRM, but its full specification and the related missing-data assumptions are not described.

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: covid-19 (2.8%), asthma (2.8%), pneumonia viral (1.3%).

The serious adverse event summaries report one affected participant in the CSJ117 0.5 mg group, none in the 1 mg group, none in the 2 mg group, one in the 4 mg group, none in the 8 mg group, and one in the placebo group. The corresponding groups at risk were 36, 37, 37, 76, 74, and 75. The posted death count is zero in every group. These are counts from the registry record, not estimates of comparative risk.

The record lists COVID-19 and asthma at 2.8% each, and viral pneumonia at 1.3%, among the leading serious adverse event terms. It also reports counts of participants with other, non-serious adverse events: 12, 14, 20, 31, 23, and 27 across the CSJ117 groups and placebo, respectively. The registry summary does not supply detail on event duration, severity grading for all events, or causal attribution. These counts should be interpreted descriptively, with attention to the different group sizes and the limits of the posted safety information.

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

The primary results describe average change in pre-dose FEV1 over the treatment period for participants in the defined Full Analysis Set. The sponsor-reported comparison for CSJ117 0.5 mg is positive, with a 95% confidence interval above zero. The estimates for the other four dose comparisons have confidence intervals that include zero. This is a statistical description of the posted analyses; it is not a recommendation about treatment and does not establish a clinical benefit.

The magnitude and precision of the estimate both matter. The estimate for the 0.5 mg group is 0.122 L relative to placebo, but the registry record does not specify what difference would be clinically important. The intervals for the remaining comparisons include both positive and negative values, so their estimates alone cannot establish whether a difference exists in either direction. The pattern across doses is not steadily increasing, and the record does not report a formal dose-response analysis.

The findings also need to be read in the context of the study design and record limitations. This was a phase 2 study listed as terminated, but the reason for termination is not reported in the registry record. The original sample-size rationale, full statistical plan, multiplicity handling, interim analyses, and missing-data sensitivity analyses are not reported. Those omissions constrain assessments of how the analyses were planned and how robust the estimates might be to alternative assumptions.

The results do not establish the effect of CSJ117 beyond the population, treatment period, outcome definitions, and analysis represented in the record. They do not establish longer-term outcomes, effects on every secondary measure, or a complete comparative safety profile. The adverse-event figures are descriptive counts, and the registry does not provide enough detail to attribute events to study treatment. These boundaries are essential when interpreting the reported estimates.

18. Why This Trial Matters Statistically

This trial is statistically informative because it places multiple doses of an inhaled investigational drug alongside a placebo comparison while measuring lung function repeatedly. The primary outcome is a continuous spirometry measure, and the reported model-based contrasts make both the estimated differences and their uncertainty visible. The separate dose comparisons also make clear why a collection of point estimates should not be mistaken for a simple dose-response pattern.

The record illustrates the importance of keeping an analysis tied to its method. A straightforward recalculation from summary statistics gives values close to, but not identical to, the sponsor’s repeated-measures results. The MMRM analysis is the sponsor’s stated primary method, so it is the appropriate basis for describing the primary findings. The difference highlights why summary-data calculations can be useful checks without replacing the planned model-based analysis.

It also shows why confidence intervals and reporting details matter. One reported primary interval lies above zero, whereas the remaining dose-comparison intervals include zero. Without information about multiplicity, the full model specification, the original sample-size rationale, and missing-data handling, readers cannot fully assess the confirmatory strength of the pattern. The terminated status is another relevant feature, but its reason is not reported in the registry record. Together, these details make the record a useful example of cautious interpretation: statistical estimates are informative, but the design and reporting context determine how much can be inferred from them.

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 identifies the primary model as MMRM but does not provide its full specification. Covariates, covariance structure, detailed missing-data rules, and sensitivity analyses are not reported. Because the primary endpoint uses repeated measurements, those modeling and data-handling details would help readers assess the robustness of the estimates.

The trial status is terminated, but the reason for termination is not reported in the registry record. The record does not state whether termination followed a prespecified rule, an operational decision, or another circumstance. It also does not report interim analyses or stopping boundaries. Without that context, the termination status cannot be linked to the primary results.

The registry lists several CSJ117 dose comparisons and many secondary measures, but it does not report the multiplicity plan or a hierarchy for interpreting these tests. The original sample-size justification and assumptions are also not reported. The planning illustrations based on observed effects are not substitutes for that original rationale and should not be used to infer what the investigators planned.

The primary endpoint’s clinical-importance threshold is not reported. Consequently, the numerical size of a difference cannot be classified as clinically meaningful from this record alone. The secondary outcomes cover different physiological and participant-reported measures, and the available summaries do not establish a single consistent pattern across outcomes. Finally, adverse-event counts are descriptive; the record does not provide enough information on event attribution and detail to establish comparative safety conclusions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Efficacy and Safety of CSJ117 in Patients With Severe Uncontrolled Asthma — NCT04410523.
• Registry record last updated 2024-06-20; status last verified 2024-06.
• Results first posted 2023-08-07.
• 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 phase 2, randomized, multicenter, double-blind, parallel-arm, placebo-controlled study of CSJ117 added to existing asthma therapy in adults with severe uncontrolled asthma. Recorded enrollment was 335, and the study status is terminated. The reason for termination is not reported in the registry record.

The primary endpoint was average change from baseline in pre-dose FEV1 at Week 8 and Week 12, assessed using an MMRM in the Full Analysis Set. The sponsor reported a positive comparison for CSJ117 0.5 mg versus placebo, with a 95% confidence interval from 0.016 to 0.229 L. The other reported dose-comparison intervals include zero. The registry also posts secondary outcome and adverse-event information. Multiplicity procedures, the original sample-size rationale, detailed missing-data methods, and the reason for termination are not reported.