A Study in Patients With Atopic Eczema to Test How Effective BI 655130 is and How Well it is Tolerated: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study in Patients With Atopic Eczema to Test How Effective BI 655130 is and How Well it is Tolerated (NCT03822832), a randomized phase 2 study. The primary outcome is Percentage Change From Baseline in the Eczema Area and Severity Index (EASI) Score at Week 16.

2. Clinical Question

3. Trial Design

This was a phase IIa, multicentre, randomized, double-blind, placebo-controlled, parallel-group trial in adults with moderate to severe atopic dermatitis. The registry lists enrollment of 51 and the study status as completed. The recorded start date is 2019-02-12, and the primary completion date is 2020-01-17. These dates describe the trial record and do not by themselves establish when every participant was assessed.

The trial compared intravenous placebo with an active arm labelled spesolimab 600 mg intravenous every 4 weeks. BI 655130 is the intervention name in the registry record. The brief objective describes repeated intravenous administrations and comparison with placebo. The record does not give enough detail in the registry record to reconstruct the full schedule of administrations or all follow-up procedures.

The primary outcome was percentage change from baseline in EASI at Week 16, with the endpoint timeframe described as baseline (day 1) and Week 16 (day 113 ±3 days), up to 116 days. The primary analysis population was the Full Analysis Set, defined as participants who were randomized, received at least one dose, and had a baseline measurement for the primary endpoint. The endpoint summaries report 12 participants in the placebo group and 28 in the spesolimab group; these arm-specific analysis counts should not be confused with the overall enrollment figure.

The registry lists 9 outcome measures and 11 analyses, with 8 secondary outcomes posted. The secondary outcomes include EASI and SCORAD change measures, EASI response thresholds, investigator global assessment, and adverse events. The original sample-size justification, allocation ratio rationale, detailed conduct of masking, and full protocol are not reported in the registry record. The stated sample-size illustrations are analytical planning calculations based on the observed effect, not descriptions of the trial’s original design.

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: All subjects were screened for eligibility prior to participation in the trial. Subjects attended a specialist site which ensured that they (the subjects) strictly met all inclusion and none of the exclusion criteria. Subjects were not to be allocated to a treatment group if any of the entry criteria were violated.

Period 1 - Double Blind Period

Reasons for not completing this period:

Re-allocation

Reasons for not completing this period:

Period 2 - Open Label Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS): All participants who were randomised, received at least one dose during the trial, and had a baseline measurement for the primary endpoint.

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: Randomized set (RS): this patient set includes all patients who were randomized into the trial. It will be used for display of patient disposition, baseline and demographic characteristics, and patients with IPDs (Important Protocol Deviations).

6. Primary Endpoint

The registry lists the primary outcome as Percentage Change From Baseline in the Eczema Area and Severity Index (EASI) Score at Week 16, measured over Baseline (day 1) and Week 16 (day 113 ±3 days), up to 116 days..

The primary endpoint is percentage change from baseline in the Eczema Area and Severity Index (EASI) score at Week 16. EASI evaluates two dimensions of atopic dermatitis: disease extent and clinical signs. It assesses four body sites and scores four signs—erythema, induration or papulation, excoriation, and lichenification—on a scale from zero to three. The total EASI score has a maximum of 72. The registry also gives suggested severity strata, ranging from clear at 0 through very severe from 50.1 to 72.0.

Using percentage change expresses the Week 16 result in relation to each participant’s baseline EASI score, rather than reporting only the Week 16 score. A negative percentage change represents a decrease from baseline. This form of endpoint can describe the relative change in a clinical measure, while the between-arm contrast addresses whether the estimated change differs between treatment groups.

EASI is used in this trial because its scoring combines disease extent and several clinical signs into a defined measure. The primary endpoint is not a direct measure of every aspect of symptoms, quality of life, or long-term disease course. The registry’s primary description concerns the EASI score at Week 16; it does not report a threshold for what magnitude of between-arm difference would be considered clinically important.

7. Results Posted in the Registry

• Spesolimab 600 mg Intravenous Every 4 Weeks: mean -37.90 versus -12.30 on control; difference -25.60 (95% CI -59.58 to 8.38), standardized effect d = -0.50; z-test p = 0.140.

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.

Absolute Change From Baseline in Eczema Area and Severity Index (EASI) at Week 4

• 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:
  • Spesolimab 600 mg Intravenous Every 4 Weeks: mean -6.30 versus -7.00 on control; difference 0.70 (95% CI -6.59 to 7.99), standardized effect d = 0.06; z-test p = 0.851.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Spesolimab 600 mg Intravenous Every 4 Weeks and the control. The interval gives the range of effects that remain compatible with the data.

Percentage Change From Baseline in Eczema Area and Severity Index (EASI) at Week 4

• 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:
  • Spesolimab 600 mg Intravenous Every 4 Weeks: mean -23.80 versus -21.60 on control; difference -2.20 (95% CI -29.68 to 25.28), standardized effect d = -0.05; z-test p = 0.875.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Spesolimab 600 mg Intravenous Every 4 Weeks and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in SCORing of Atopic Dermatitis (SCORAD) at Week 4

• 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:
  • Spesolimab 600 mg Intravenous Every 4 Weeks: mean -13.20 versus -13.30 on control; difference 0.10 (95% CI -16.99 to 17.19), standardized effect d = 0.00; z-test p = 0.991.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Spesolimab 600 mg Intravenous Every 4 Weeks and the control. The interval gives the range of effects that remain compatible with the data.

The secondary endpoints cover EASI change and response at earlier and later visits, SCORAD change, investigator global assessment, and adverse events. The posted continuous Week 4 comparisons for EASI and SCORAD have estimates close to zero relative to the uncertainty represented by their reported intervals. Taken together, these early continuous-measure comparisons do not provide a more precise or definitive picture than the primary Week 16 result.

The Week 4 findings are temporally distinct from the primary endpoint at Week 16, and the measures are not identical. Absolute EASI change, percentage EASI change, and SCORAD change use different scales or summaries; response thresholds and investigator global assessment are categorical outcomes. They should not be treated as interchangeable replications of the primary analysis.

The registry lists more secondary outcomes than the continuous results described in the registry entries. The available secondary results therefore do not support a complete account of every listed endpoint. No unreported outcome result should be inferred from the fact that an outcome was registered.

Multiple testing matters because examining several outcomes and time points creates more opportunities for apparently noteworthy results to arise by chance. Unless a testing strategy accounts for multiplicity, an individual secondary p-value has less evidential weight than a single prespecified primary test. The registry record does not report a multiplicity adjustment or a hierarchy for the secondary outcomes. Accordingly, secondary results are best viewed as contextual and exploratory rather than as independent confirmation of the primary finding.

Overall, the secondary outcome set adds information about different measures and time points, but does not remove the uncertainty in the Week 16 primary comparison. The reported pattern should be interpreted alongside the primary estimate, its confidence interval, and the limits of the posted secondary results.

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

• Number of Patients With Drug Related Adverse Events (AEs)
• Absolute Change From Baseline in Eczema Area and Severity Index (EASI) at Week 4
• Percentage Change From Baseline in Eczema Area and Severity Index (EASI) at Week 4
• Proportion of Patients With a 50% Improvement From Baseline in Eczema Area and Severity Index (EASI)(EASI50) at Week 4 and 16
• Proportion of Patients With a 75% Improvement From Baseline in Eczema Area and Severity Index (EASI)(EASI75) at Week 4 and 16
• Change From Baseline in SCORing of Atopic Dermatitis (SCORAD) at Week 4
• Change From Baseline in SCORing of Atopic Dermatitis (SCORAD) at Week 16
• Number of Patients Achieving at Least a 2-grade Reduction From Baseline to Clear (0) or Almost Clear (1) in Investigator's Global Assessment (IGA) at Week 4 and 16

9. Statistical Interpretation

10. Statistical Methods Explained

How was the primary comparison estimated?

The registry reports a restricted maximum likelihood (REML)-based Mixed Model for Repeated Measures (MMRM). In general, a repeated-measures model can use measurements collected at multiple visits while representing how measurements from the same participant may be related over time. REML is a method for estimating variance and covariance components in a statistical model. The registry specifies an unstructured covariance matrix, which allows the model to estimate a separate covariance for each pair of repeated measurement occasions rather than imposing a simpler pattern. This flexibility can be useful, although the registry record does not report diagnostics or the model’s convergence details.

The listed fixed categorical effects were treatment, visit, Asian/Non-Asian status, and the treatment-by-visit interaction. The continuous fixed covariates were baseline endpoint and the baseline-by-visit interaction. In general, including baseline and visit terms can account for baseline measurement and allow estimated trajectories to vary over visits; the treatment-by-visit term allows the estimated treatment contrast to depend on visit. The registry identifies these model terms but does not report additional model-selection decisions or sensitivity analyses.

What does an adjusted mean represent?

The arm values are least-squares means from the primary model. In general, a least-squares mean is a model-based estimate adjusted for the variables included in the model, rather than a simple arithmetic average of all observed values. The reported mean difference compares the model estimates for the two arms at the endpoint. The model-based result is therefore the appropriate reported estimate to prioritize over a calculation reconstructed from arm summaries.

The registry’s primary population is the Full Analysis Set. It includes randomized participants who received at least one dose and had a baseline measurement for the primary endpoint. This definition differs from an intention-to-treat definition that necessarily includes every randomized participant regardless of treatment received or baseline availability. The registry record does not provide a participant flow account or explain the exclusions between enrollment and the endpoint analysis counts.

Why are the recalculated statistics different in kind?

The unadjusted recalculation uses the posted arm estimates and standard errors to approximate a pooled standard deviation and then derive a simple contrast. Such calculations can be useful as a transparent check on the scale of the result, but they do not reproduce the MMRM. They omit the reported covariate adjustment and the model’s repeated-measures covariance structure. Their uncertainty estimates and p-values can therefore differ from the sponsor’s model-based results, even when a point estimate is numerically similar. The recalculation is labeled as such and should not be substituted for the reported analysis.

Confidence intervals describe uncertainty around an estimated contrast under a specified statistical model. A wider interval indicates less precision, all else equal. The reported primary interval is a 90% interval; the unadjusted recalculation uses a 95% interval. Since the intervals arise from different approaches and confidence levels, comparing their endpoints as if they were identical measures would be misleading.

What cannot be learned from the reported method?

The registry record does not report how missing outcome measurements were handled, the assumptions made about missingness, or sensitivity analyses for departures from those assumptions. A repeated-measures model can analyze available observations under particular modeling assumptions, but the mere use of MMRM does not establish how missing data were addressed in practice. Details such as imputation, estimand definition, and robustness analyses are not reported in the registry record.

The record also does not report the trial’s original sample-size calculation, interim analyses, or a complete statistical analysis plan. The planning illustrations elsewhere are based on observed effects and specified assumptions; they are not evidence of what the sponsor used when designing this trial. The primary endpoint is identified, but the registry entries do not establish whether any unreported analysis decisions were made before or after access to outcome data.

General statistical interpretation requires separating the model estimate, its uncertainty, and the decision context. The mean difference gives an estimated contrast on the percentage-change scale. The confidence interval conveys precision under the analysis model. The p-value summarizes compatibility with a null contrast under that model and its assumptions. None of these quantities alone establishes clinical importance or resolves limitations in the available data.

11. Confidence Intervals and Precision

The primary mixed-model estimate is a mean difference of -25.6, with a 90% confidence interval from -54.9 to 3.7. The interval includes zero, so the reported data do not sharply distinguish a negative contrast from no difference or a contrast in the other direction. The point estimate is only one location within a broad range of values compatible with the model and data.

A confidence interval is a range produced by a statistical procedure that, under its assumptions and repeated use, is designed to cover the underlying parameter at its stated confidence level. It is not a range containing a specified proportion of individual participant outcomes, and it is not a probability statement that the true effect falls inside this particular interval. The interval’s width is relevant because it indicates that the estimated treatment contrast is not very precise.

The primary endpoint arm summaries include standard errors of 14.3 for placebo and 9.8 for spesolimab. Standard errors describe uncertainty in estimated means, not the spread of individual participant measurements. They should not be read as standard deviations. The reported model-based confidence interval and the arm standard errors answer related but different questions.

The recalculation gives a 95% confidence interval from -59.58 to 8.378. It differs from the reported 90% interval both because it uses a different confidence level and because it is based on an unadjusted approximation rather than the reported repeated-measures model. The two intervals should not be combined or treated as alternative outputs from one identical analysis. The registry’s mixed-model estimate remains the reported analysis for the primary endpoint.

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 illustrations are planning calculations based on the observed effect, not the trial’s original design assumptions. For the continuous outcomes in this record, the figures are participants per arm, not total events. The calculations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original design assumptions are not reported in the registry record.

The column for 80% power gives the number of participants per arm that the planning calculation indicates would provide an 80% chance of detecting the selected effect under those assumptions, if that effect and model assumptions held. The 90% power column uses the same idea with a higher target chance of detection. These are design-planning quantities, not probabilities that the observed trial result is correct. This is not observed power.

Rows using 100%, 75%, and 50% of the observed effect illustrate how the target effect size changes the planning result. Smaller effects are harder to distinguish from random variation, so detecting them generally requires more participants. The listed figures are hypothetical planning illustrations, not recommended enrollment targets or proof that a future trial will achieve its target power. The calculations do not account for any design features beyond the assumptions stated in the registry entries.

The planning numbers can be especially sensitive when the observed difference is small relative to estimated variability. They should be read as illustrations of the relationship between effect size, sample size, and target power—not as a retrospective judgment of the completed trial’s performance. No original sample-size justification is 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 = -25.600; pooled standard deviation σ = 51.196.
2. n = 2 × (1.96 + 0.842)² × 51.196² / -25.600² = 62.8, rounded up to 63 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 <- -25.6                      # observed difference in means
sigma <- 51.1959393949004                     # 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(3822832)
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 = 63 (80% power), 85 (90% power)
 75% of observed effect: n per arm = 112 (80% power), 150 (90% power)
 50% of observed effect: n per arm = 252 (80% power), 337 (90% power)
power.t.test: 63.8 
Simulated power at n = 63 per arm: 0.793 (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 reports the primary mixed-model analysis as a mean difference of -25.6, a 90% confidence interval from -54.9 to 3.7, and p = 0.149. This is the sponsor-reported analysis and uses the stated repeated-measures model. It is the primary result to use when describing the trial’s reported statistical analysis.

The unadjusted recalculation from the arm summaries also estimates a mean difference of -25.6, but its 95% confidence interval is -59.58 to 8.378 and its p-value is 0.14. It is an approximate, unadjusted calculation and does not reproduce the sponsor’s MMRM. Similarity in the point estimate should not obscure the differences in confidence level, covariate adjustment, and modeling method.

The record indicates no discrepancy between the recalculated and reported point estimates under its comparison convention. That does not mean every statistic matches: the intervals and p-values differ because the calculations are not identical. The registry-reported model remains the appropriate account of the sponsor’s analysis, while the recalculation serves only as a simple check based on posted summary statistics.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint: percentage change from baseline in EASI at Week 16. It also lists multiple secondary outcomes, including several measurements at different visits and more than one type of outcome. When many hypotheses are tested, the chance of at least one apparently unusual result can increase. Statistical methods can address this issue through prespecified testing hierarchies or adjustments, but such a plan is not reported in the registry record.

The registry entries do not identify whether secondary tests were adjusted for multiplicity, whether any formal hierarchy was used, or how confirmatory versus exploratory endpoints were distinguished in the analysis plan. As a result, individual secondary p-values should not be interpreted as if each were the sole planned test. The record also does not report interim analyses or whether any interim testing rules were specified.

Missing-data handling is another uncertainty. The primary population definition requires a baseline measurement, and the primary endpoint summaries have fewer participants in each arm than the registry’s overall enrollment figure. However, the reasons for the difference are not reported in the registry record. The record does not describe the amount or pattern of missing Week 16 data, the missingness assumptions, any imputation procedure, or sensitivity analyses. MMRM is identified as the primary method, but that label alone does not establish the missing-data assumptions or demonstrate that they are appropriate.

The Full Analysis Set is defined as randomized participants who received at least one dose and had a baseline measurement for the primary endpoint. The registry does not provide enough information to compare this population with other analysis populations or to assess results under alternative populations. The detailed statistical analysis plan and original sample-size justification are also not reported in the registry record. These omissions limit assessment of how prespecified the modeling and testing decisions were, and how robust the conclusions are to alternative assumptions.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypersensitivity (5.6%), cardiac failure (4.5%), osteoarthritis (4.5%), abortion spontaneous (4.5%), pulmonary hypertension (4.5%).

The registry reports serious adverse event counts for three exposure periods or groups. In the placebo period, 1 serious adverse event was reported among 18 participants at risk. In the spesolimab treatment period, 3 were reported among 33 at risk. In the open-label spesolimab period, 3 were reported among 22 at risk. Deaths were reported as 0 in each listed group. The record also reports other adverse event counts separately; serious and other adverse events should not be conflated.

These are descriptive counts for the recorded groups and periods. The groups and observation windows differ, and the open-label period is distinct from the randomized placebo-controlled period. The counts alone do not establish that an event was caused by treatment, and they do not give a complete comparative risk estimate. The registry lists serious-event terms including hypersensitivity, cardiac failure, osteoarthritis, abortion spontaneous, pulmonary hypertension, and acute myocardial infarction with the associated percentages, but those listings do not by themselves establish causality or comparative rates.

Interpretation is limited by the available exposure counts, periods, and absence of further event-level detail in the registry entries. These safety figures should be read as recorded adverse-event summaries, not as a basis for medical advice or a definitive safety comparison.

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

The primary result estimates a larger decrease in EASI percentage change in the spesolimab arm than in the placebo arm, based on the reported point estimate. However, the 90% confidence interval includes zero and spans a wide range of possible contrasts. The statistical result is therefore uncertain: it does not establish a precise between-arm difference, nor does it prove that there was no difference.

A p-value of 0.149 does not measure the probability that treatment is effective, and it is not a measure of clinical importance. The confidence interval and point estimate should be read together. The estimate conveys the direction and magnitude observed in the model; the interval conveys uncertainty around that estimate under the model’s assumptions. The registry does not report a threshold defining a clinically important difference in this endpoint.

The findings apply to this phase IIa trial, its population, treatment schedule, analysis population, and follow-up as recorded. They do not automatically generalize to people outside the adult moderate to severe atopic dermatitis population described, to different dosing schedules, or to longer-term outcomes. The trial’s enrollment and endpoint analysis counts also constrain how much can be inferred about precision and representativeness.

The safety summaries are descriptive. Adverse events recorded during the listed periods do not establish treatment causality, and the registry entries do not provide enough information to characterize every potential safety outcome. Similarly, secondary endpoints provide additional context but do not eliminate uncertainty in the primary comparison, particularly when no multiplicity procedure is reported.

Overall, the posted results show an estimated primary contrast favoring a greater decrease in the active arm on the EASI percentage-change scale, but with substantial statistical uncertainty. They do not by themselves establish a clinically meaningful benefit, prove absence of effect, or support a treatment decision. The result is best understood as an estimate from a relatively small phase IIa study requiring cautious interpretation.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate should not be interpreted without its confidence interval. The estimated primary mean difference is -25.6, but the reported 90% interval extends from -54.9 to 3.7. A single estimate can appear clear in isolation; the interval makes visible that the data are compatible with substantially different values, including no difference.

It also highlights the distinction between a model-based clinical-trial analysis and a simple calculation reconstructed from summary statistics. The registry’s MMRM accounts for repeated measurements and includes specified covariates, whereas the recalculation is unadjusted and approximate. Similar point estimates do not make the analyses equivalent, and their uncertainty measures are not directly interchangeable.

The trial is also useful for understanding how secondary endpoints and multiple testing affect interpretation. Several measures and visits can contribute context, but without a reported multiplicity strategy, isolated secondary findings carry less weight as confirmatory evidence. A broad endpoint set does not automatically make the primary result more certain.

Finally, the record distinguishes enrollment from the analysis population and records safety events across different periods. Those distinctions matter: the denominator for an endpoint analysis need not match enrollment, and adverse-event counts across different exposure periods should not be treated as one uniform randomized comparison. The registry entries do not explain every difference, so statistical interpretation must remain bounded by what the record reports.

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 endpoint analysis includes arm-specific counts of 12 and 28, while overall enrollment is listed as 51. The registry record does not explain the reasons for these differences or provide a participant flow account. Without that information, it is difficult to assess the role of missing endpoint data, exclusions, or other analysis-population decisions.

The primary result has a broad 90% confidence interval that includes zero. This limits precision about the treatment contrast. The trial is described as phase IIa, and its enrollment is modest in relation to the broad range of effects compatible with the interval. The registry does not report the original sample-size justification, so it is not possible to assess the planned precision or power from the trial’s design assumptions.

Several analysis details are not reported: missing-data methods and assumptions, sensitivity analyses, multiplicity procedures, interim analyses, and a complete statistical analysis plan. The registry identifies the MMRM specification, but not its diagnostics, convergence information, or robustness checks. These gaps limit independent assessment of the primary model and secondary analyses.

The posted secondary outcomes are incomplete relative to the listed outcome set, and multiple visits and measures raise multiplicity concerns. Safety counts come from distinct recorded periods, including an open-label period, and should not be treated as a single randomized comparison. The registry entries also do not establish adverse-event causality or provide a detailed assessment of longer-term safety. These limitations constrain the conclusions that can be drawn from the posted record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study in Patients With Atopic Eczema to Test How Effective BI 655130 is and How Well it is Tolerated — NCT03822832.
• Registry record last updated 2025-10-20; status last verified 2025-10.
• Results first posted 2022-12-01.
• 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

NCT03822832 is a completed phase IIa, multicentre, randomized, double-blind, placebo-controlled parallel-group trial in adults with moderate to severe atopic dermatitis. The registry lists BI 655130 as the intervention and reports enrollment of 51. The primary endpoint was percentage change from baseline in EASI at Week 16, analyzed in the Full Analysis Set using an REML-based MMRM.

The reported primary mean difference was -25.6, with a 90% confidence interval from -54.9 to 3.7 and p = 0.149. The interval includes zero and indicates uncertainty about the size and direction of the contrast. Secondary outcomes and safety summaries add context but are limited by incomplete posted results, unreported multiplicity and missing-data procedures, and differing analysis and exposure groups. The record supports a cautious description of the estimates, not a definitive clinical conclusion.