A Study of Lebrikizumab in Combination With Topical Corticosteroids in Patients With Atopic Dermatitis (AD) That Are Not Adequately Controlled With or Are Non-eligible for Cyclosporine: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Lebrikizumab in Combination With Topical Corticosteroids in Patients With Atopic Dermatitis (AD) That Are Not Adequately Controlled With or Are Non-eligible for Cyclosporine (NCT05149313), a randomized phase 3 study. The primary outcome is Double-blind Induction Period: Percentage of Participants Who Achieved Eczema Area and Severity Index (EASI) 75 (>=75% Reduction From Baseline in EASI Score) at Week 16.

2. Clinical Question

The clinical question concerns the added treatment assignment during the blinded induction period, rather than a comparison of lebrikizumab with no background treatment. Both groups received topical corticosteroids. The record describes the study as randomized, placebo-controlled, quadruple-masked, and parallel-group. Its stated primary purpose was to evaluate efficacy compared with placebo up to Week 16. The registry record does not report what clinical difference investigators considered important before the trial began, nor does it report the original sample-size justification.

3. Trial Design

This was a randomized, parallel-group, phase 3 trial with quadruple masking and a placebo control. The registry reports an enrollment of 331 participants. The two double-blind induction groups were lebrikizumab plus topical corticosteroids and matching placebo plus topical corticosteroids. The primary endpoint was assessed at Week 16, and the stated main purpose focused on efficacy through that time point.

The intervention descriptions specify subcutaneous treatment. In the lebrikizumab group, participants received two 250 mg injections at Baseline and Week 2, followed by one 250 mg injection every two weeks during induction through Week 16. The placebo group received matching placebo every two weeks during the 16-week induction period. The record also describes an open-label maintenance period through Week 52, including groups continuing lebrikizumab and participants moving from placebo to lebrikizumab. The available arm description for the lebrikizumab group is truncated, so further details of that regimen are not reported in the registry record.

The primary endpoint population was the full analysis set: all randomized participants, analyzed under the treatment group to which they were assigned. The primary arm counts were 220 for lebrikizumab plus topical corticosteroids and 111 for placebo plus topical corticosteroids. The trial is marked completed. Its recorded start date is 2021-12-23 and its primary completion date is 2023-01-30.

The registry record does not report the randomization procedure, any stratification factors, the planned allocation ratio, or the original sample-size assumptions. It also does not describe the full protocol for handling treatment discontinuation, rescue treatment, or missing Week 16 measurements. Those details should not be inferred from the observed group sizes or from the reported statistical method.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: A total of 368 participants were screened, of which 331 participants were randomized into 2 treatment arms (Lebrikizumab and Placebo). The study has 2 treatment periods: a 16-week double-blind Induction Period and 36-week open-label Maintenance Period.

Double-blind Induction Period (16-weeks)

Reasons for not completing this period:

Open-label Maintenance Period (36 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS included all randomized participants and were analyzed under the treatment group as randomized.

5. Baseline Characteristics

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

Population: Full Analysis Set (FAS) included all randomized participants and were analyzed under the treatment group as randomized.

6. Primary Endpoint

The registry lists the primary outcome as Double-blind Induction Period: Percentage of Participants Who Achieved Eczema Area and Severity Index (EASI) 75 (>=75% Reduction From Baseline in EASI Score) at Week 16, measured over At Week 16.

The primary endpoint was the percentage of participants who achieved EASI 75 at Week 16. EASI is the Eczema Area and Severity Index, a composite measure of the severity and extent of atopic dermatitis. It evaluates erythema, infiltration, excoriation, and lichenification across the head, trunk, upper limbs, and lower limbs. Clinical signs are graded on a four-point scale from absent to severe, while affected area is assessed by body region. The total score ranges from 0 to 72, with higher scores indicating more severe or extensive disease.

EASI 75 is a responder definition: a participant counts as an achiever if the EASI score has fallen by at least 75% from that participant’s baseline score. The endpoint therefore reduces each participant’s change to a yes-or-no outcome for the Week 16 assessment. The reported percentage is the proportion meeting that threshold in each treatment group.

A threshold-based endpoint can make a result easier to interpret as the share of participants reaching a substantial prespecified degree of improvement. It does not show the full distribution of score changes, how far participants above the threshold improved, or how close non-achievers came to it. Those details are not reported for the primary outcome in the registry record. The endpoint addresses skin signs and extent as measured by EASI; it does not, by itself, describe every aspect of symptoms, quality of life, or treatment experience.

7. Results Posted in the Registry

• Double-blind Induction Period: Lebrikizumab +TCS: 68.2% (150/220) versus 40.5% (45/111) on control; risk difference 27.6 percentage points (95% CI 16.6 to 38.7), risk ratio 1.68 (1.32–2.14); unadjusted two-proportion 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.

Double-blind Induction Period: Percentage of Participants Who Achieved Investigator Global Assessment (IGA) Score of 0 or 1 and 2-point Improvement at Week 16

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Double-blind Induction Period: Lebrikizumab +TCS: 41.8% (92/220) versus 24.3% (27/111) on control; risk difference 17.5 percentage points (95% CI 7.2 to 27.8), risk ratio 1.72 (1.20–2.47); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Double-blind Induction Period: Lebrikizumab +TCS than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Double-blind Induction Period: Percentage of Participants Who Achieved a 4-point Improvement in Pruritus Numeric Rating Score (NRS) at Week 16

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Double-blind Induction Period: Lebrikizumab +TCS: 49.7% (99/199) versus 29.4% (30/102) on control; risk difference 20.3 percentage points (95% CI 9.1 to 31.6), risk ratio 1.69 (1.21–2.36); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Double-blind Induction Period: Lebrikizumab +TCS than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Double-blind Induction Period: Percentage of Participants Who Achieved a 4- Point Improvement in Skin Pain NRS at Week 16

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Double-blind Induction Period: Lebrikizumab +TCS: 51.4% (89/173) versus 27.3% (24/88) on control; risk difference 24.2 percentage points (95% CI 12.3 to 36.1), risk ratio 1.89 (1.30–2.73); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Double-blind Induction Period: Lebrikizumab +TCS than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The numerical secondary outcomes posted for the blinded induction period follow the same general direction as the primary result: the reported response percentages are higher in the lebrikizumab plus topical corticosteroids group than in the placebo plus topical corticosteroids group. These outcomes cover different domains, including investigator-rated skin status and participant-reported itch and skin pain. They provide additional context, but they are not interchangeable with the primary EASI 75 endpoint.

The registry lists a broader set of planned secondary outcomes, including other EASI thresholds and quality-of-life measures. Numerical results for those outcomes are not reported in the registry record in the information available for this analysis. The three posted numerical secondary summaries should not be taken to represent all secondary outcomes or to establish consistency across every planned measure.

Secondary findings generally carry less inferential weight when many outcomes are assessed and no adjustment for multiple comparisons is reported. Testing numerous endpoints increases the chance that at least one result may appear statistically notable even when there is no underlying effect for that endpoint. The registry record does not report a multiplicity-control strategy, hierarchy, or confirmatory status for the secondary tests. Their p-values should therefore be read as reported findings, not as proof that the full family of outcomes has been controlled for false-positive results.

The registry reports sponsor analyses for the IGA and itch outcomes, while no sponsor-reported analysis is listed for the skin-pain endpoint. The posted secondary numerical results also have separate denominators for some measures. The reasons for those denominators, and whether missing measurements or endpoint-specific eligibility account for them, are not reported in the registry record. Taken together, the secondary results are supportive context for interpreting the primary finding, but they do not replace it or resolve questions about multiplicity and missing data.

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

• Double-blind Induction Period: Percentage of Participants Who Achieved Investigator Global Assessment (IGA) Score of 0 or 1 and 2-point Improvement at Week 16
• Double-blind Induction Period: Percentage of Participants Who Achieved a 4-point Improvement in Pruritus Numeric Rating Score (NRS) at Week 16
• Double-blind Induction Period: Percentage of Participants Who Achieved EASI 75 (>=75% Reduction From Baseline in EASI Score) at Weeks 2, 4, 8, and 12
• Double-blind Induction Period: Percentage of Participants Who Achieved EASI 90 (>=90% Reduction From Baseline in EASI Score) at Weeks 2, 4, 8, 12 and 16
• Double-blind Induction Period: Percentage of Participants Who Achieved EASI 50 (>=50% Reduction From Baseline in EASI Score) at Weeks 2, 4, 8, 12 and 16
• Double-blind Induction Period: Percentage of Participants Who Achieved a 4-point Improvement in Dermatology Life Quality Index (DLQI) at Weeks 2, 4, 8, 12 and 16
• Double-blind Induction Period: Percentage of Participants Who Achieved a 4-point Improvement in Children's Dermatology Life Quality Index (CDLQI) at Weeks 2, 4, 8, 12 and 16
• Double-blind Induction Period: Percentage of Participants Who Achieved a 4- Point Improvement in Skin Pain NRS at Week 16

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each person either achieved EASI 75 at Week 16 or did not. For a binary outcome, the group percentage is the number meeting the definition divided by the number analyzed for that outcome. In the primary summary, the posted groups included 220 participants assigned to lebrikizumab plus topical corticosteroids and 111 assigned to placebo plus topical corticosteroids. The registry lists 68.4% and 40.8% as the corresponding outcome percentages.

What does a risk difference describe?

A risk difference subtracts the event proportion in one group from the event proportion in the other. It expresses the contrast on the absolute probability scale, rather than as a relative comparison. The recalculated risk difference for the primary outcome is 0.276. This estimate is based on the posted event counts and group sizes: 150 of 220 in the lebrikizumab group and 45 of 111 in the placebo group. Because it is an unadjusted calculation, it does not necessarily reproduce a model-based or stratified analysis reported by the sponsor.

Other ways to compare binary outcomes include a risk ratio, which compares the proportions as a ratio, and an odds ratio, which compares odds rather than probabilities. These measures answer related but different questions. The registry’s own primary analysis is reported as a difference in percentages using the Cochran-Mantel-Haenszel method, so that result should be distinguished from the simple risk-difference recalculation.

What does the registry-reported method do?

The Cochran-Mantel-Haenszel method is commonly used to estimate or test a treatment-group association across strata. In general, it combines information across defined strata rather than treating all observations as one unstratified comparison. The particular strata, any stratification factors, and their role in the analysis are not reported in the registry record. It is therefore not possible to infer which factors the sponsor accounted for from the method name alone.

The registry reports a difference in percentages of 27.88, a 95% confidence interval from 15.63 to 40.14, and p < 0.001 for the primary endpoint. The reported analysis is labelled a superiority analysis. A superiority test evaluates whether the data are inconsistent with a null hypothesis of no difference in the specified direction or contrast, under the assumptions of the analysis. The label does not determine whether a difference is clinically important; that judgment requires context not included in the registry record.

How should a confidence interval and p-value be read?

A confidence interval gives a range of values compatible with the data and the method’s assumptions, at the stated confidence level. It reflects sampling uncertainty, not all possible sources of uncertainty. A narrower interval indicates greater statistical precision for the estimated contrast; a wider interval indicates less precision. The p-value quantifies how unusual data at least as incompatible with the null hypothesis would be if that hypothesis and the analysis assumptions held. It does not state the chance that the observed result arose by chance, and it is not a measure of treatment benefit.

For the primary endpoint, the unadjusted recalculation gives a 95% confidence interval from 0.166 to 0.387 and p < 0.001. The sponsor-reported analysis gives a different estimate and interval because it is a distinct method. The registry record does not report enough detail to explain every difference between the two results. Since the record marks discrepancy as false, the recalculation is not identified as conflicting with the reported analysis, but it should still be read as an unadjusted calculation rather than as the sponsor’s method.

Why does the analysis population matter?

The primary endpoint description says that the full analysis set included all randomized participants and that participants were analyzed according to their assigned treatment. This approach preserves the randomized group assignment in the analysis and is commonly intended to retain the benefits of randomization. The record does not state whether every randomized participant contributed an observed Week 16 measurement, how missing outcome data were addressed, or whether any participants were excluded from the primary analysis. These details matter because a percentage based on observed outcomes can be affected if outcome availability differs between groups.

The registry also describes secondary binary outcomes, such as reaching IGA response thresholds or achieving specified symptom improvements. The same broad ideas apply to those endpoints: the event definition determines who counts as a responder, the analyzed denominator determines the percentage, and the comparison method determines the estimate and uncertainty. The secondary outcomes are separate questions and should not be treated as multiple measurements of precisely the same construct.

11. Confidence Intervals and Precision

The primary sponsor-reported estimate is a difference in percentages of 27.88, with a 95% confidence interval from 15.63 to 40.14. This interval describes the range of contrasts compatible with the reported method and data under the method’s assumptions. The lower and upper limits are both above zero, so the reported interval does not include a null difference.

The unadjusted recalculation gives a risk difference of 0.276, with a 95% confidence interval from 0.166 to 0.387. This interval also excludes zero. It is tied to the simple count-based comparison and should not be substituted for the sponsor’s reported interval. The two analyses use different approaches, and the registry record does not provide details sufficient to reconcile every difference between their estimates and limits.

Confidence intervals describe statistical precision, not clinical importance. Whether the range of plausible contrasts would matter to participants depends on clinical context and a threshold for meaningful benefit, neither of which is reported in the registry record. The intervals also do not account for every uncertainty, including possible effects of missing data, outcome measurement, or choices made in the analysis plan.

The primary endpoint groups had unequal sizes: 220 and 111 participants. The observed proportions and intervals should be understood in that context. A confidence interval is not a guarantee that the true effect lies inside its limits; rather, it is a procedure that would cover the target value at the stated rate across repeated studies under its assumptions. The posted interval provides a useful summary of sampling precision for this trial’s Week 16 comparison, but not a prediction of the result in another population or study.

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 planning figures are participants per arm, not total events. They are illustrations based on the observed effect, not the trial’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculations consider detecting the full observed effect, 75% of the observed effect, or 50% of the observed effect.

For the primary endpoint, planning for 100% of the observed effect gives 50 participants per arm for 80% power and 67 participants per arm for 90% power. Planning for 75% of the observed effect gives 91 participants per arm for 80% power and 121 participants per arm for 90% power. Planning for 50% of the observed effect gives 204 participants per arm for 80% power and 273 participants per arm for 90% power.

In plain language, the 80% power column gives the approximate number per arm for a study with an 80% chance of detecting the specified effect under the stated assumptions, if that effect is real. The 90% power column uses a higher target chance of detection and therefore generally requires more participants. Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants per arm. These planning figures are not observed power and do not describe the chance that this completed trial’s result is correct.

The registry record does not report the trial’s own original sample-size assumptions, the effect size anticipated during planning, or whether the trial’s actual design used these calculations. The illustrations also assume equal allocation, whereas the reported primary groups were not equal in size. They should be used to understand how the assumed effect and power target change planning needs, not as a reconstruction of the trial’s design process.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.405; treatment proportion p₁ = 0.682; average p̄ = 0.544.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7044 = 1.3806.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6768 = 0.5696.
4. n = (1.3806 + 0.5696)² / (0.2764)² = 49.8, rounded up to 50 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
p0 <- 0.405405405405405                          # control proportion
p1 <- 0.681818181818182                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(5149313)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 50 (80% power), 67 (90% power)
 75% of observed effect: n per arm = 91 (80% power), 121 (90% power)
 50% of observed effect: n per arm = 204 (80% power), 273 (90% power)
power.prop.test: 49.8 
Simulated power at n = 50 per arm: 0.816 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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-reported primary analysis used the Cochran-Mantel-Haenszel method and reported a difference in percentages of 27.88, with a 95% confidence interval from 15.63 to 40.14 and p < 0.001. That is the analysis reported in the registry for the primary endpoint.

The recalculation is a simple, unadjusted comparison based on posted event counts and group sizes. It gives a risk difference of 0.276, a 95% confidence interval from 0.166 to 0.387, and p < 0.001. It is not a reproduction of the sponsor’s Cochran-Mantel-Haenszel analysis. Because the registry record does not report the analysis strata or other details needed to reproduce that method, the recalculation cannot establish why the estimates and intervals differ.

The sponsor result and the recalculation point in the same direction and both intervals exclude zero, but they should remain separately labelled. The record marks discrepancy as false, so it does not identify a conflict requiring the sponsor’s result to be set aside. The sponsor’s reported analysis remains the trial’s reported inferential result; the unadjusted calculation is a transparent check based on the posted summaries, with the limitations of that approach.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 19 outcome measures and reports 3 analyses. It includes several secondary endpoints assessed during the double-blind induction period, with outcomes spanning EASI thresholds, investigator assessment, itch, pain, and quality of life. Testing multiple endpoints creates a multiplicity issue: without an analysis strategy that controls the overall chance of false-positive conclusions, the evidential strength of individual secondary p-values can be overstated.

The registry record does not report whether the trial used a prespecified testing sequence, a family-wise error adjustment, another multiplicity procedure, or a distinction between confirmatory and exploratory secondary endpoints. This absence does not show that no such plan existed; it means the approach is not reported in the registry record. The primary endpoint is identified, but the record does not supply enough statistical-plan detail to determine how the full set of outcomes was handled.

The primary population is described as the full analysis set, including all randomized participants analyzed according to randomized treatment. That is useful information about group assignment in the analysis. However, the record does not report the number with observed primary endpoint data by group, the handling of missing Week 16 assessments, or the assumptions and procedures used for any imputation. Missingness could matter if availability of outcome measurements differed between groups or was related to participants’ outcomes.

The secondary outcome denominators are not identical across every posted result. The registry record does not explain the reasons for the differences. It also does not report a detailed accounting of participants who discontinued, withdrew, or lacked assessments, nor whether the denominator reflects all randomized participants or a subset for each secondary outcome. These uncertainties limit evaluation of how robust the percentages are to missing data and how directly different endpoint estimates can be compared.

The record does not report the original sample-size justification, interim analyses, or a complete statistical analysis plan. Those items should not be inferred from the final enrollment, the p-values, or the planning illustrations. Their absence from the registry record limits the ability to assess prespecification and analysis choices, but does not by itself establish that a particular procedure was or was not used.

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: cutaneous t-cell lymphoma (1.0%), autoimmune thyroiditis (1.0%), abdominal pain (1.0%), uterine polyp (1.0%), diabetes mellitus (0.9%).

During the double-blind induction period, the registry lists serious adverse events for 3 of 220 participants in the lebrikizumab plus topical corticosteroids group and 1 of 111 participants in the placebo plus topical corticosteroids group. It lists other adverse events for 84 of 220 and 31 of 111 participants, respectively. No deaths are listed in either induction group.

The open-label maintenance groups are reported separately: the lebrikizumab-to-lebrikizumab group had 12 serious adverse events among 212 participants and 108 other adverse events among 212; the placebo-to-lebrikizumab group had 4 serious adverse events among 100 participants and 48 other adverse events among 100. No deaths are listed in either maintenance group. These groups belong to a different treatment period and are not directly equivalent to the randomized induction comparison.

The serious-event terms with the highest listed percentages include cutaneous T-cell lymphoma, autoimmune thyroiditis, abdominal pain, and uterine polyp at 1.0% each, and diabetes mellitus and asthma at 0.9% each. The registry record does not provide enough context in these summaries to assess causality, timing, exposure duration, or whether events were considered related to treatment. Event counts alone do not establish comparative safety or rule out uncommon risks.

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

The primary result describes a higher posted percentage achieving EASI 75 at Week 16 in the lebrikizumab plus topical corticosteroids group than in the placebo plus topical corticosteroids group. It is a comparison between randomized assignments during the blinded induction period, in a population with moderate-to-severe atopic dermatitis and the specified cyclosporine-related eligibility criteria.

The result does not mean every participant in the lebrikizumab group achieved the endpoint, or that participants who did not achieve it had no improvement. EASI 75 is a threshold: it records whether a participant crossed a specified level of reduction from baseline, not the full amount or pattern of change. The group percentages do not show individual trajectories or the distribution of responses.

The trial compared lebrikizumab plus topical corticosteroids with placebo plus topical corticosteroids. It does not isolate the effect of topical corticosteroids, compare lebrikizumab alone with no treatment, or establish how the treatment groups would compare under a different background regimen. The primary time point was Week 16; longer-term comparative conclusions cannot be drawn from the primary endpoint alone.

Statistical evidence and clinical importance are related but distinct. The confidence intervals and p-values describe uncertainty and compatibility with a null difference under specified methods. The registry record does not report a threshold for a clinically important difference, so the clinical importance of the observed contrast cannot be determined from statistical significance alone.

The result also does not answer every question about safety, quality of life, symptom burden, or outcomes beyond the posted measures. Secondary results provide additional but more limited context, especially because a multiplicity strategy and missing-data procedures are not reported. The findings apply most directly to the enrolled population, assigned treatments, and recorded study period, rather than automatically extending to people who would not have met the trial’s eligibility criteria.

18. Why This Trial Matters Statistically

This trial illustrates why the estimand and outcome definition matter in clinical statistics. The primary endpoint is not a mean change in EASI; it is the percentage of participants crossing a responder threshold. That makes the result interpretable as a group share meeting a defined improvement criterion, while omitting information about the degree of improvement within each responder and the amount of change among non-responders.

It also illustrates why estimates from different analysis methods need clear labels. The sponsor-reported Cochran-Mantel-Haenszel result and the simple unadjusted recalculation both compare the randomized groups, but they use different methods and produce different numerical estimates and intervals. Reporting both without conflating them helps readers distinguish the trial’s stated analysis from a calculation based on summary counts.

Precision is central to interpreting a contrast. The confidence intervals convey a range of values compatible with each analysis, while the p-values address a different question about the null hypothesis. Neither alone determines whether a difference matters to patients. The registry does not report a clinical importance threshold, so statistical significance should not be treated as a substitute for that context.

The record also highlights limitations that arise when a registry summary omits statistical-plan details. The full handling of missing outcomes, multiplicity across secondary endpoints, and original sample-size assumptions is not reported. Those details affect how readers assess the strength and scope of inferences, even when the primary comparison is clearly identified.

Finally, both randomized groups received topical corticosteroids. A careful interpretation preserves that comparison rather than attributing the entire between-group contrast to a treatment in isolation. Keeping the population, background treatment, endpoint, time point, analysis method, and uncertainty together is essential for a statistically faithful reading.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not report the original sample-size justification or the assumptions used when planning enrollment. The sample-size illustrations based on the observed effect cannot fill that gap, because they are not the trial’s design calculations. The record also does not report interim analyses or the complete statistical analysis plan.

Details needed to reproduce the sponsor’s primary analysis are incomplete. Although the Cochran-Mantel-Haenszel method is named, the strata or factors used are not reported. The sponsor-reported estimate and the simple unadjusted recalculation therefore cannot be fully reconciled from the registry record alone.

Missing-data handling is another uncertainty. The primary population is described as all randomized participants analyzed as assigned, but the record does not provide the number with observed Week 16 outcomes by group or explain how missing measurements were addressed. Some secondary outcomes have different denominators, and the reasons are not reported. These omissions limit assessment of whether availability of measurements could have influenced the posted percentages.

The registry lists multiple secondary outcomes but does not report a multiplicity strategy. Consequently, the inferential status of secondary p-values is unclear. Numerical findings are also absent from the record for many listed outcomes, limiting a broad assessment of whether results were consistent across all planned measures.

Safety summaries provide event counts and selected serious-event terms, but the registry information does not establish causality or provide enough detail about timing, exposure, or event adjudication for a complete comparative assessment. The primary endpoint is limited to a Week 16 responder threshold and does not describe the full distribution of EASI change or longer-term comparative outcomes. These are limitations of what the registry record reports, not proof that additional information was unavailable elsewhere.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Lebrikizumab in Combination With Topical Corticosteroids in Patients With Atopic Dermatitis (AD) That Are Not Adequately Controlled With or Are Non-eligible for Cyclosporine — NCT05149313.
• Registry record last updated 2025-05-20; status last verified 2025-04.
• Results first posted 2024-11-06.
• 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

The registry describes a completed randomized, quadruple-masked, parallel-group phase 3 trial of lebrikizumab plus topical corticosteroids versus matching placebo plus topical corticosteroids during a 16-week double-blind induction period. Enrollment was 331. The study population comprised adults and adolescents with moderate-to-severe atopic dermatitis that was not adequately controlled with cyclosporine or for whom cyclosporine was not medically advisable.

The primary endpoint was the percentage achieving EASI 75 at Week 16. The posted percentages were 68.4% and 40.8% in the lebrikizumab and placebo groups, respectively. The sponsor-reported comparison was a 27.88 difference in percentages, with a 95% confidence interval from 15.63 to 40.14 and p < 0.001. A separate unadjusted recalculation gives a risk difference of 0.276, with a 95% confidence interval from 0.166 to 0.387 and p < 0.001.

The record also lists secondary outcomes, safety summaries, and an open-label maintenance period through Week 52. Original sample-size assumptions, detailed missing-data procedures, multiplicity handling, and several analysis-plan details are not reported in the registry record.