Evaluation of the Efficacy and Safety of Lebrikizumab (LY3650150) in Moderate to Severe Atopic Dermatitis (ADvocate1): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of the Efficacy and Safety of Lebrikizumab (LY3650150) in Moderate to Severe Atopic Dermatitis (ADvocate1) (NCT04146363), a randomized phase 3 study. The primary outcome is Percentage of Participants With an Investigator Global Assessment (IGA) Score of 0 or 1 and a Reduction ≥2 Points From Baseline to Week 16.

2. Clinical Question

The trial record describes a 52-week study, with a 16-week induction period followed by a 36-week long-term maintenance period. The primary comparison concerns the induction-period endpoint, rather than the maintenance regimens. The posted primary result is a between-group comparison of the percentage reaching the defined IGA threshold by Week 16.

3. Trial Design

ADvocate1 (NCT04146363) is recorded as a Phase 3, randomized, parallel-group trial of lebrikizumab and placebo in people with moderate to severe atopic dermatitis. The record describes the study as double-blind and lists quadruple masking. Eli Lilly and Company is named as the sponsor. Enrollment was 424 participants. The study is marked completed, with a start date of 2019-09-24 and primary completion date of 2021-06-21.

The trial was designed to assess lebrikizumab as monotherapy. Its 52-week duration was divided into a 16-week induction period and a 36-week maintenance period. During induction, the primary active-treatment group received lebrikizumab 250 mg every two weeks after loading doses, while the placebo group received placebo. The posted primary outcome is assessed from Baseline to Week 16, at the end of induction.

The record also describes several maintenance pathways, including blinded maintenance assignments and an open-label escape arm for some participants. Those pathways are not the same comparison as the primary Week 16 placebo-controlled analysis. The specific maintenance-arm descriptions include treatment switching or differing schedules; they should not be treated as a single continued randomized comparison without additional details.

The registry record does not report the original sample-size justification, the planned number of participants in each primary-analysis group as a design target, or details of any interim analyses. It also does not report the full statistical analysis plan. Those details should not be inferred from the enrollment count or the planning illustrations based on observed results.

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.

Only the first 6 of 11 groups are shown.

Induction Period

Reasons for not completing this period:

Maintenance Blinded Treatment Period

Reasons for not completing this period:

Maintenance Open Label Escape Arm

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants, even if the participant does not take the assigned treatment, does not receive the correct treatment, or otherwise does not follow the protocol. Markov Chain Monte Carlo Multiple Imputation (MCMC-MI) was used to handle missing data.

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: All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With an Investigator Global Assessment (IGA) Score of 0 or 1 and a Reduction ≥2 Points From Baseline to Week 16, measured over Baseline to Week 16.

The primary endpoint is the percentage of participants with an Investigator Global Assessment (IGA) score of 0 or 1 and a reduction of at least 2 points from Baseline to Week 16. The IGA is an investigator’s global rating of atopic dermatitis severity, using a static 5-point scale from 0, clear skin, to 4, severe disease. The rating considers erythema, papulation or induration, oozing or crusting, and lichenification.

This endpoint requires both a low absolute severity score at Week 16 and a change from the participant’s own Baseline score. That combination distinguishes reaching a relatively clear state from merely having some improvement, while the reduction criterion also makes the endpoint responsive to change over time. It is a binary outcome for each participant: either the stated threshold is met or it is not. The group-level result is the percentage meeting that threshold.

The endpoint is clinically interpretable as a proportion reaching a predefined investigator-rated state, but it does not describe every aspect of disease severity or symptom burden. Other posted outcomes include measures of eczema extent and pruritus, which address different dimensions of the condition.

7. Results Posted in the Registry

• Lebrikizumab Q2W: 43.1% (122/283) versus 12.8% (18/141) on control; risk difference 30.3 percentage points (95% CI 22.4 to 38.3), risk ratio 3.38 (2.15–5.31); 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.

Percentage of Participants With an IGA Score of 0 or 1 and a Reduction ≥2 Points From Baseline to Week 2

• 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:
  • Lebrikizumab Q2W: 2.5% (7/283) versus 0.7% (1/141) on control; risk difference 1.8 percentage points (95% CI -0.5 to 4.0), risk ratio 3.49 (0.43–28.07); unadjusted two-proportion z-test p = 0.208.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lebrikizumab Q2W and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With an IGA Score of 0 or 1 and a Reduction ≥2 Points From Baseline to Week 4

• 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:
  • Lebrikizumab Q2W: 10.6% (30/283) versus 0.7% (1/141) on control; risk difference 9.9 percentage points (95% CI 6.0 to 13.7), risk ratio 14.95 (2.06–108.48); 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 Lebrikizumab Q2W than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With an IGA Score of 0 or 1 and a Reduction ≥2 Points From Baseline to Week 16 in Adults

• 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:
  • Lebrikizumab Q2W: 42.3% (104/246) versus 11.4% (14/123) on control; risk difference 30.9 percentage points (95% CI 22.6 to 39.2), risk ratio 3.71 (2.22–6.21); 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 Lebrikizumab Q2W than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several aspects of atopic dermatitis, including IGA thresholds at earlier visits, EASI response and change, and pruritus ratings and improvement. They complement the primary Week 16 IGA endpoint by addressing other time points and different dimensions of symptoms or disease severity. Their presence helps describe the range of outcomes the trial tracked, but the registry record does not provide results for every listed secondary outcome in the detail available for the highlighted comparisons.

Among the posted secondary comparisons described in detail, the Week 2 IGA threshold result is small and uncertain: the sponsor-reported risk-difference interval spans zero. The Week 4 comparison and the adult Week 16 IGA comparison have sponsor-reported intervals above zero. These results are directionally consistent with the primary endpoint for the later and adult comparisons, while the earliest time point is less conclusive. The values and detailed per-endpoint interpretations belong with their respective results rather than being repeated.

Secondary outcomes generally carry less confirmatory weight than a prespecified primary endpoint. When many outcomes or analyses are examined, the chance of at least one apparently notable finding can increase. A multiplicity procedure can address this issue, but the registry record does not report whether secondary testing was adjusted, whether outcomes were tested in a hierarchy, or which analyses were designated confirmatory. It would therefore be inappropriate to treat every secondary p-value as if it had the same evidential status as the primary result.

The record lists 40 outcome measures and 45 analyses, and 38 secondary outcomes are posted. Those counts show that the results span a broad analysis set, but they do not disclose the testing sequence or adjustment strategy. The secondary findings are best viewed as context for the primary result, with caution about multiplicity and incomplete reporting of the statistical plan.

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

• Percentage of Participants With an IGA Score of 0 or 1 and a Reduction ≥2 Points From Baseline to Week 2
• Percentage of Participants With an IGA Score of 0 or 1 and a Reduction ≥2 Points From Baseline to Week 4
• Percentage of Participants With an IGA Score of 0 or 1 and a Reduction ≥2 Points From Baseline to Week 16 in Adults
• Percentage of Participants Achieving EASI-90 (≥90% Reduction in EASI Score) From Baseline to Week 16
• Percent Change in Pruritus Numerical Rating Scale (NRS) Score From Baseline to Week 16
• Percentage of Participants With a Pruritus NRS Score of ≥4-points at Baseline Who Achieve a ≥4-point Reduction in Pruritus NRS Score From Baseline to Week 16
• Percentage of Participants With a Pruritus NRS Score of ≥5-points at Baseline Who Achieve a ≥4-point Reduction in Pruritus NRS Score From Baseline to Week 16
• Percent Change in EASI Score From Baseline to Week 16

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: the participant either met the Week 16 IGA threshold or did not. A group percentage summarizes the frequency of that event. The percentage is not a continuous measure of average severity, and it does not show how far beyond the threshold participants may have improved.

What does the risk difference express?

A risk difference compares the event proportions in two groups by subtracting one group’s proportion from the other’s. It is expressed on an absolute scale, which makes it possible to describe how separated the observed event rates are. The sponsor reported the primary risk difference as 29.7 percentage points. Its confidence interval gives a range of values compatible with the data under the analysis assumptions. The registry’s reported interval is 21.6 to 37.8 percentage points.

A risk difference is distinct from a relative measure such as a risk ratio or odds ratio. Absolute and relative measures answer different questions and can give different impressions of the same data. The sponsor’s reported primary analysis is on the risk-difference scale, so that is the most direct scale for describing the posted comparison. No additional relative interpretation is needed to understand the primary result.

Why use a Cochran-Mantel-Haenszel analysis?

The sponsor identifies the primary comparison method as Cochran-Mantel-Haenszel. In general, this method can estimate an association or treatment contrast across strata, while accounting for the stratification used in an analysis. The registry record does not identify the strata or describe the detailed implementation for this endpoint. It would therefore be inappropriate to infer which factors were included or how the estimates were constructed beyond the method named in the record.

The reported analysis is a superiority analysis. In general, a superiority test assesses whether the observed evidence is inconsistent with no difference in the specified direction or on the chosen contrast scale. A p-value describes how compatible the data are with the null model, conditional on the analysis assumptions; it is not the probability that the null hypothesis is true and does not measure the size or clinical importance of an effect. The reported p-value for the primary comparison is below 0.001.

What does the recalculation add?

A recalculated comparison uses the posted group summaries to form a simple, unadjusted estimate. It is useful as a transparent descriptive check, but it is not necessarily numerically identical to a sponsor analysis that uses a stratified method, imputation, or other specified procedures. The methods and populations need to match before differences between estimates can be interpreted. The registry record does not report a discrepancy between the recalculation and the sponsor result. The sponsor’s own analysis remains the main inferential result.

The primary population is described as all randomized participants, including those who did not take assigned treatment, received the wrong treatment, or otherwise did not follow the protocol. This description makes the primary analysis inclusive of randomized participants rather than restricted to those who fully adhered to treatment. It does not, by itself, provide every detail needed to reconstruct the analysis population or estimand.

How was missing information addressed?

The record states that Markov Chain Monte Carlo multiple imputation (MCMC-MI) was used to handle missing data for the primary outcome. In general, multiple imputation represents missing values through repeated plausible imputations, analyzes each completed dataset, and combines the results to reflect uncertainty due to missingness. This approach depends on assumptions about the missing-data process and the imputation model. The registry record does not report the variables in the model, the number of imputations, diagnostic checks, or sensitivity analyses. Those unreported details limit independent assessment of the missing-data handling.

More generally, randomization supports a comparative design by assigning participants to treatment groups at random, but the interpretation still depends on outcome definition, follow-up, missing-data methods, and the analysis plan. The registry record identifies several of these elements, but does not report the full plan or all implementation details. Statistical results should therefore be read in the context of what is explicitly documented.

11. Confidence Intervals and Precision

The confidence intervals around the arm-level primary percentages are 37.1% to 49.0% for lebrikizumab Q2W and 7.0% to 18.5% for placebo. These intervals show uncertainty around each group’s estimated percentage. They are not ranges containing a fixed proportion of individual participant outcomes, nor do they mean that every value in the interval is equally likely.

For the between-group comparison, the sponsor-reported 95% confidence interval for the risk difference is 21.6 to 37.8 percentage points. Its lower and upper limits are both above zero, so the interval is consistent with a positive difference on the reported scale. The interval also conveys precision: a narrower interval would indicate less statistical uncertainty, while a wider one would indicate more. The interval still allows a range of effect sizes, rather than identifying one exact effect.

Confidence intervals depend on the analysis method and its assumptions. The sponsor’s interval is attached to the reported Cochran-Mantel-Haenszel analysis, whereas an unadjusted recalculation may use a different method. For that reason, intervals from different approaches should not be treated as interchangeable. The registry record does not provide enough detail to assess every assumption underlying the sponsor’s interval.

The arm-level intervals overlap, but overlap of separate group intervals is not the formal test of the difference. The sponsor’s reported comparison and its confidence interval address the between-group contrast directly. The relevant interval for that contrast is the risk-difference interval, not a visual comparison of the two arm-specific intervals.

Statistical precision does not establish how important a difference is to patients, and a confidence interval does not address all possible bias. Its interpretation is conditional on the design, outcome measurement, analysis population, and missing-data method.

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 illustrations express sample size as participants per arm, not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These are planning assumptions for the illustration; the original trial’s design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm needed, under those assumptions, for an 80% chance of detecting the assumed effect if that effect were the true one. The 90% power column gives the corresponding estimated participants per arm for a 90% chance. Higher power generally requires a larger planned sample, all else being equal. The entries are planning illustrations, not observed power.

Rows that plan for 100%, 75%, or 50% of the observed effect ask how many participants per arm would be needed if the effect targeted for detection were the full observed effect or a smaller fraction of it. Smaller effects are harder to distinguish from random variation, so they require more participants. This is why planning for a smaller fraction of the observed effect leads to larger sample-size estimates.

The planning numbers are not evidence that the trial was originally designed around those assumptions, and they should not be read as the trial’s actual enrollment target. The registry record reports enrollment of 424, but the original design rationale is not reported. A sample-size curve, when read as a planning aid, should likewise be interpreted as displaying how the estimated requirement changes with the assumed effect and power, rather than as a description of observed trial performance.

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 = 0.128; treatment proportion p₁ = 0.431; average p̄ = 0.279.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6345 = 1.2437.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5972 = 0.5026.
4. n = (1.2437 + 0.5026)² / (0.3034)² = 33.1, rounded up to 34 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 <- 0.127659574468085                          # control proportion
p1 <- 0.431095406360424                          # 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(4146363)
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 = 34 (80% power), 44 (90% power)
 75% of observed effect: n per arm = 55 (80% power), 73 (90% power)
 50% of observed effect: n per arm = 110 (80% power), 146 (90% power)
power.prop.test: 33.1 
Simulated power at n = 34 per arm: 0.828 (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 reports the primary analysis using the Cochran-Mantel-Haenszel method, with a risk difference of 29.7 percentage points, a 95% confidence interval from 21.6 to 37.8, and a p-value below 0.001. This is the trial’s own reported inferential analysis and is the appropriate primary result to cite when describing the registry finding.

The recalculation is a simple unadjusted analysis derived from the posted arm-level summaries. It provides a check on the broad direction and scale of the comparison, but it does not reproduce every feature of the sponsor’s method. In particular, an unadjusted calculation should not be mistaken for the stratified sponsor analysis or presumed to account for the same details of missing data and analysis implementation.

The discrepancy indicator is false, so the record does not flag a conflict between these results. Even without a flagged discrepancy, the two estimates arise from different procedures and need not be identical. Where a discrepancy is present, the sponsor’s own analysis takes precedence; the same principle keeps the sponsor-reported method as the main reference. The recalculation is supplemental, not a competing replacement.

The registry record does not describe the strata used in the sponsor analysis or provide a full statistical analysis plan. The sponsor result can therefore be reported as recorded, while detailed reproduction of the analysis is not possible from the registry description alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and reports 40 outcome measures and 45 analyses, with 38 secondary outcomes posted. Multiple outcomes create a multiplicity issue: as more hypotheses are tested, the probability of finding one apparently unusual result by chance can rise. In general, investigators may address this by adjusting significance thresholds, using a prespecified testing hierarchy, or distinguishing confirmatory outcomes from exploratory ones. The registry record does not report whether any such approach was used for the secondary outcomes.

The sponsor reports a superiority analysis for the primary endpoint, but the full statistical analysis plan is not reported in the registry record. The record does not describe whether the primary endpoint was tested within a broader multiplicity-control procedure, how secondary tests were ordered, or whether subgroup analyses were prespecified. These omissions limit assessment of how strongly individual secondary findings should be interpreted as confirmatory evidence.

For the primary outcome, the stated analysis population includes all randomized participants even if they did not take the assigned treatment, did not receive the correct treatment, or otherwise did not follow the protocol. This is a broad randomized population definition. The registry also states that MCMC-MI was used to handle missing data. In general, multiple imputation addresses missing outcome information by replacing it with values generated under a statistical model and incorporating uncertainty across imputations.

The record does not report the imputation model, its assumptions, the number of imputed datasets, or sensitivity analyses testing departures from those assumptions. It also does not describe the amount or pattern of missing primary outcome data. Without those details, readers cannot judge how sensitive the endpoint estimate might be to the handling of missingness. No further assumptions about missing-data mechanisms or protocol deviations should be inferred from the description alone.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (25.0%), dysmenorrhoea (2.3%), cholecystitis (1.6%), somatic symptom disorder (1.6%), micromastia (1.0%).

The registry lists serious adverse event counts separately for induction, blinded maintenance, and escape-arm groups. During induction, serious adverse events were reported for 1 of 141 participants in the placebo group and 6 of 282 participants in the lebrikizumab 250 mg Q2W group. These are counts within the listed groups, not adjusted comparisons. No deaths are recorded in any of the listed adverse-event groups.

Maintenance and escape-arm groups have different denominators and treatment histories. For example, the listed serious-event counts range from none to small counts across those groups, which include participants assigned to different maintenance schedules or entered into escape treatment. These groups should not be combined into a single comparison without further information, because the record describes distinct pathways and the same trial participants may have passed through multiple periods.

The registry also lists other adverse events, which are distinct from serious adverse events. The posted counts are descriptive and do not by themselves establish causation, comparative risk, or the clinical significance of each event. Details such as event definitions, exposure-adjusted rates, and a complete account of how events were collected are not reported in the registry record. These figures should be interpreted as safety summaries within the recorded groups, not as a stand-alone evaluation of overall safety.

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

The primary result describes the proportion of randomized participants who met a particular investigator-rated skin-severity threshold at Week 16. In this trial, the lebrikizumab Q2W group had a higher observed percentage meeting that threshold than the placebo group, and the sponsor-reported risk-difference confidence interval was above zero. This is a statistical description of the posted comparison in the induction period.

The result does not mean that every participant in the lebrikizumab group met the endpoint, or that no participant in the placebo group did. It also does not describe the size or nature of improvement for each participant who did not meet the threshold. A binary endpoint compresses a range of clinical experiences into whether a defined criterion was reached.

The finding is limited to the population, endpoint, treatment schedule, and follow-up interval described in the registry record. It does not establish the comparative result for every maintenance pathway, every outcome, or time beyond the primary Week 16 assessment. It also does not answer how participants valued the observed changes or whether the outcome captures all symptoms that matter to them.

Statistical evidence is not the same as a complete assessment of benefit and harm. The safety record includes serious adverse event counts for several trial periods, but those counts do not by themselves establish causality or provide a full comparison of risks. Missing-data assumptions, multiplicity, and details of the statistical plan also affect how confidently the broader set of findings can be interpreted. The registry record does not report all of those details.

Accordingly, the posted result supports a narrow conclusion about the Week 16 IGA endpoint in this randomized comparison. It should not be expanded into a blanket claim about treatment effects, long-term outcomes, or all patients with atopic dermatitis.

18. Why This Trial Matters Statistically

This trial illustrates why an endpoint definition matters. The primary measure combines an absolute IGA state at Week 16 with a required reduction from Baseline. Those criteria make the outcome more informative than either a final score or change alone, but they also mean the result depends on how investigators rate severity and on each participant’s starting score.

It also provides an example of reporting both group-level percentages and a direct between-group contrast. The arm percentages describe how often the endpoint occurred in each group; the risk difference describes their absolute separation. A confidence interval around that contrast communicates uncertainty more directly than a p-value alone, and the sponsor’s analysis reports both.

The analysis record raises practical questions common to clinical trial interpretation: how to distinguish sponsor-reported results from unadjusted checks, how missing outcomes are handled, and how to interpret secondary analyses when many outcomes are recorded. Here, the registry names the primary method and missing-data approach, but does not report enough detail to reproduce every step or assess all assumptions.

The study’s design also separates induction from maintenance. A Week 16 primary result should not automatically be generalized to later maintenance strategies, particularly when the record describes several pathways after induction. Keeping the endpoint, time period, and analysis population explicit helps prevent a narrow statistical comparison from being read as a broader conclusion than it supports.

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 full statistical analysis plan, original sample-size justification, planned interim analyses, or design assumptions for the trial’s enrollment. The sample-size illustrations based on the observed effect do not fill those gaps. Without the original planning rationale, the enrollment count cannot be used to infer what effect the study was designed to detect.

The primary endpoint is investigator-rated and dichotomized at a specified threshold. The registry describes the scale and clinical features considered, but the posted result does not show the full distribution of IGA scores or the magnitude of change for participants who did not cross the endpoint threshold. This limits the detail available about the range of responses.

The registry states that MCMC-MI handled missing primary outcome data, but does not report missing-data quantities, the imputation model, or sensitivity analyses. Those omissions make it difficult to assess how robust the primary estimate is to assumptions about missing outcomes. The analysis population is described broadly, but other implementation details are not reported.

Multiplicity is another limitation for interpreting the wider outcome set. The record lists many measures and analyses but does not specify whether secondary testing was adjusted or organized in a prespecified hierarchy. Secondary findings therefore should not automatically receive the same confirmatory interpretation as the primary analysis.

Finally, the Week 16 endpoint is an induction-period result, while the overall study continued through Week 52 and included multiple maintenance and escape pathways. The primary comparison alone does not characterize those later treatment paths. The registry record does not provide enough information to treat their groups as a single, directly comparable continuation of the initial randomized contrast.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of the Efficacy and Safety of Lebrikizumab (LY3650150) in Moderate to Severe Atopic Dermatitis (ADvocate1) — NCT04146363.
• Registry record last updated 2022-11-30; status last verified 2022-11.
• Results first posted 2022-08-29.
• 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

ADvocate1 (NCT04146363) was a completed, randomized, parallel-group, quadruple-masked Phase 3 trial sponsored by Eli Lilly and Company. It enrolled 424 participants with moderate to severe atopic dermatitis and evaluated lebrikizumab against placebo. The record describes a double-blind, placebo-controlled study lasting 52 weeks, with a 16-week induction period and a 36-week maintenance period.

The primary outcome was the percentage meeting the IGA score and improvement threshold from Baseline to Week 16. The sponsor-reported analysis found a risk difference of 29.7 percentage points, with a 95% confidence interval from 21.6 to 37.8 and a p-value below 0.001. The primary population included all randomized participants, and MCMC-MI was used for missing data.

The record reports multiple secondary outcomes and safety summaries across induction, maintenance, and escape groups. The original sample-size justification, full statistical analysis plan, and details of multiplicity control are not reported in the registry record.