Efficacy & Safety of Nemolizumab in Subjects With Moderate-to-Severe Atopic Dermatitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy & Safety of Nemolizumab in Subjects With Moderate-to-Severe Atopic Dermatitis (NCT03989349), a randomized phase 3 study. The primary outcome is Percentage of Participants With Investigator's Global Assessment (IGA) Success at Week 16: Intent-To-Treat (ITT) Population.

2. Clinical Question

The trial asked whether nemolizumab was associated with a different proportion of participants meeting a prespecified investigator-assessed response at Week 16 than placebo. The population was adults and adolescents with moderate-to-severe atopic dermatitis that was not adequately controlled with topical treatments. The primary outcome used the intent-to-treat population, defined in the registry record as all randomized participants.

The registry record describes a randomized, double-blind, placebo-controlled study. Random allocation supports a between-group comparison, while masking is intended to reduce the influence of expectations on treatment delivery and assessment. The posted primary results are percentages meeting the endpoint and a sponsor-reported stratified difference. The comparison concerns this particular endpoint and time point; it does not, by itself, answer every question about symptoms, longer-term outcomes, or safety.

3. Trial Design

This was a Phase 3, randomized, quadruple-masked, parallel-group, placebo-controlled study sponsored by Galderma R&D. The registry lists an enrollment of 787 and a completed status. The recorded start date was 2019-06-30, and the primary completion date was 2022-02-23. Participants were adults and adolescents with moderate-to-severe atopic dermatitis not adequately controlled with topical treatments.

For the initial treatment period, the posted arms were nemolizumab 30 mg and placebo, both administered by subcutaneous injection. The primary outcome was assessed at Week 16. The registry record says data were planned to be collected and analyzed for the Initial Treatment Period. Its definition of the intent-to-treat population is all randomized participants, and it specifies that missing Week 16 primary outcome data were considered non-response.

The design is described as parallel-group: participants were assigned to a study arm rather than receiving both initial-period treatments in sequence. The masking designation is quadruple, although the record excerpt does not identify the roles of the masked parties. Further details of the randomization procedure, allocation concealment, stratification factors, visit schedule, adherence, or handling of treatment discontinuation are not reported in the registry record.

The record also lists maintenance-period safety groups, including groups continuing nemolizumab at different schedules and groups assigned to placebo. Those later groups have different treatment histories and are not the same simple initial-period comparison. The original protocol’s sample-size justification and planned analysis details beyond those explicitly recorded are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: A total of 787 randomized 2:1 to receive either nemolizumab or placebo.At Week 16, 235 nemolizumab treated participants were clinical responders(IGA of 0\[clear\] or 1\[almost clear\]or Eczema Area and Severity Index \[EASI\]-75) re-randomized to receive nemolizumab Q4,nemolizumab Q8W,or placebo during Maintenance Period.85 participants received placebo in Initial Treatment, responded to placebo at Week 16,re-assigned to placebo and continued to receive placebo Q4W in Maintenance Period.

Initial Treatment(Day 1-Week 16 Predose)

Reasons for not completing this period:

Maintenance Period (Week 16-Week 48)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT population consisted of all randomized participants. Data was planned to be collected and analyzed for Initial Treatment Period.

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: The ITT population consisted of all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Investigator's Global Assessment (IGA) Success at Week 16: Intent-To-Treat (ITT) Population, measured over Week 16.

The primary endpoint was the percentage of participants with Investigator’s Global Assessment (IGA) success at Week 16 in the intent-to-treat population. IGA success required an IGA score of 0, meaning clear, or 1, meaning almost clear, together with at least a 2-grade improvement from baseline. The IGA is a 5-point scale ranging from 0 (clear) to 4 (severe), used by an investigator or trained designee to assess overall atopic dermatitis severity and clinical response.

This endpoint combines an assessment of the participant’s state at Week 16 with a required improvement relative to baseline. It is therefore more specific than simply reaching a particular score: both the final score and the change from baseline matter. Reporting the result as a percentage makes the outcome interpretable as the proportion of participants meeting this binary definition in each arm.

According to the registry definition, receipt of any rescue therapy made subsequent data treatment failure, and participants with missing Week 16 data were considered non-responders. These rules affect how the endpoint is counted and mean that the outcome is not limited to observed scores among participants with complete assessments. The registry record does not report additional details about the scale’s measurement properties or explain why this endpoint was selected over other measures.

7. Results Posted in the Registry

• Initial Treatment Period (Baseline - Week 16 Predose): Nemolizumab 30 mg: 37.7% (197/522) versus 26.0% (69/265) on control; risk difference 11.7 percentage points (95% CI 5.0 to 18.4), risk ratio 1.45 (1.15–1.83); 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 Improvement of >=4 Points in Weekly Average Peak Pruritus Numeric Rating Scale (PP NRS) at Week 16: ITT Population

• 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:
  • Initial Treatment Period (Baseline - Week 16 Predose): Nemolizumab 30 mg: 41.0% (214/522) versus 18.1% (48/265) on control; risk difference 22.9 percentage points (95% CI 16.6 to 29.2), risk ratio 2.26 (1.72–2.98); 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 Initial Treatment Period (Baseline - Week 16 Predose): Nemolizumab 30 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Improvement of >=4 Points in Weekly Average Peak Pruritus Numeric Rating Scale (PP NRS) at Week 16: Severe Pruritus Population

• 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:
  • Initial Treatment Period (Baseline - Week 16 Predose): Nemolizumab 30 mg: 48.4% (153/316) versus 21.3% (35/164) on control; risk difference 27.1 percentage points (95% CI 18.7 to 35.4), risk ratio 2.27 (1.66–3.11); 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 Initial Treatment Period (Baseline - Week 16 Predose): Nemolizumab 30 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With <2 Points in Weekly Average PP NRS at Week 16: ITT Population

• 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:
  • Initial Treatment Period (Baseline - Week 16 Predose): Nemolizumab 30 mg: 28.4% (148/522) versus 11.3% (30/265) on control; risk difference 17.0 percentage points (95% CI 11.6 to 22.5), risk ratio 2.50 (1.74–3.60); 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 Initial Treatment Period (Baseline - Week 16 Predose): Nemolizumab 30 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes extend the primary comparison to itch intensity and sleep disturbance. They include improvement thresholds on the weekly average Peak Pruritus Numeric Rating Scale, a low-score threshold on that scale, and improvement in Sleep Disturbance Numeric Rating Scale. The outcomes are reported for the intent-to-treat population and, for some itch outcomes, a severe-pruritus population. Taken as a group, the posted comparisons generally favor a higher response proportion in the nemolizumab arm than in the placebo arm.

This broad direction is consistent with the primary IGA result, but the measures capture different aspects of the condition. IGA success is an investigator-assessed global severity response, while pruritus and sleep outcomes concern participant-reported symptom dimensions. Agreement across different types of measures can provide a more rounded description of the trial, but it does not make the endpoints interchangeable or establish that every outcome has the same interpretation.

Some secondary outcomes have more than one sponsor-reported adjusted analysis in the registry record, without enough information in the excerpt to determine why multiple estimates appear. The results should therefore be read in the context of their specific populations and analysis definitions, rather than selectively combining estimates.

Multiplicity also matters. When many outcomes and analyses are examined, the chance of finding at least one small p-value by chance can increase. The registry record lists 18 outcome measures and 20 analyses, but the multiplicity strategy for the secondary outcomes is not reported in the registry record. Consequently, unadjusted or otherwise unqualified secondary results carry less confirmatory weight than a prespecified primary endpoint with a clearly described analysis. They remain useful as supporting and descriptive findings, with appropriate caution about repeated testing.

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

• Percentage of Participants With Improvement of >=4 Points in Weekly Average Peak Pruritus Numeric Rating Scale (PP NRS) at Week 16: ITT Population
• Percentage of Participants With Improvement of >=4 Points in Weekly Average Peak Pruritus Numeric Rating Scale (PP NRS) at Week 16: Severe Pruritus Population
• Percentage of Participants With <2 Points in Weekly Average PP NRS at Week 16: ITT Population
• Percentage of Participants With <2 Points in Weekly Average PP NRS at Week 16: Severe Pruritus Population
• Percentage of Participants With an Improvement of Sleep Disturbance Numeric Rating Scale (SD NRS) >=4 at Week 16: ITT Population
• Percentage of Participants With an Improvement of Sleep Disturbance Numeric Rating Scale (SD NRS) >=4 at Week 16: Severe Pruritus Population
• Percentage of Participants With Improvement of >=4 Points in Weekly Average Peak Pruritus Numeric Rating Scale (PP NRS) at Week 4: ITT Population
• Percentage of Participants With Improvement of >=4 Points in Weekly Average Peak Pruritus Numeric Rating Scale (PP NRS) at Week 4: Severe Pruritus Population

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the IGA success definition at Week 16 or did not. The posted arm percentages describe the observed proportion classified as a responder under the registry’s endpoint rules. The unadjusted recalculation compares those proportions without stratification. The sponsor also reports a stratified analysis, so the two estimates answer related but not identical statistical questions.

What does a risk difference describe?

In general, a risk difference is the event proportion in one group minus the event proportion in the comparison group. It expresses an absolute difference on the probability scale. The recalculated estimate for the primary endpoint is 0.117. It uses the posted summary counts and group sizes, without adjustment for strata. This estimate should not be confused with a relative measure, such as a risk ratio or odds ratio, which expresses the comparison on a different scale.

Why might adjustment change the estimate?

The sponsor reports a Cochran-Mantel-Haenszel analysis and labels its result a strata-adjusted percentage difference. In general, this method combines information across strata to estimate a group contrast while accounting for the stratification structure. Adjustment can yield an estimate that differs from a crude comparison if the distribution of outcomes varies across strata. The registry excerpt does not name the strata or describe the detailed model, so the adjusted result cannot be independently reconstructed from the information reported there.

How should p-values be understood?

In general, a p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. It is not the probability that treatment has no effect, and it does not convey the magnitude or practical importance of an effect. The posted unadjusted primary p-value is 0.001; the sponsor’s adjusted primary p-value is 0.001. They come from different analyses and should be identified as such rather than treated as duplicate values from one calculation.

The record identifies the sponsor method for the primary result as Cochran-Mantel-Haenszel, but the full statistical analysis plan is not reported in the registry record. In particular, the particular strata, any covariate adjustment beyond stratification, and the detailed handling of analysis populations beyond the stated intent-to-treat definition are not specified in this record excerpt.

What does the endpoint rule do?

The registry definition classifies participants receiving rescue therapy as treatment failures for subsequent data and treats missing Week 16 observations as non-response. In general, such rules make the endpoint definition explicit and avoid restricting the result to participants with an observed successful assessment. They also mean that the result reflects both the clinical response definition and the rule for assigning outcomes after rescue therapy or missing data. A complete-case analysis would answer a different question and could be vulnerable to bias if missingness is related to outcome; the registry record does not report a complete-case primary analysis.

The primary population is the intent-to-treat population, defined as all randomized participants. In general, analyzing participants according to their randomized groups preserves the comparability created by randomization, although the exact treatment of post-randomization events depends on the endpoint and analysis rules. The posted endpoint’s failure assignments are part of that definition. The record does not provide enough detail to assess adherence, treatment switching, or other post-randomization events beyond the rescue-therapy rule.

Why are the confidence intervals useful?

In general, a confidence interval gives a range of values compatible with the data and the method at a stated confidence level. Its width communicates statistical precision: narrower intervals indicate less uncertainty under the model, while wider intervals indicate greater uncertainty. The sponsor’s primary interval is reported at 97.5% confidence, from 4.6 to 19.8 for the strata-adjusted percentage difference. The interval concerns the adjusted percentage difference, not a relative measure or an individual participant’s outcome.

The interval and p-value are related summaries of the same analysis, but neither captures all limitations. Their interpretation depends on the analysis method, endpoint definition, and assumptions. Statistical precision does not establish clinical importance, and a confidence interval does not account automatically for unreported sources of bias or multiplicity.

What do the planning illustrations represent?

In general, a sample-size calculation asks how many participants would be needed under stated assumptions to have a specified chance of detecting a chosen effect using a stated significance threshold. The planning illustrations use the observed effect or a stated fraction of it, a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The planning entries are participants per arm, not total participants or event counts. They are not the trial’s original design justification. The record does not report the original sample-size assumptions.

For binary outcomes, the event is the endpoint being met, such as IGA success. General considerations include the assumed event proportions, effect size, allocation, significance threshold, and power target. If the true effect is smaller than the effect used for planning, more participants are generally needed to detect it with the same power, all else equal. The assumptions and observed effects are illustrations, not guarantees about a future study.

Secondary outcomes may have their own estimates and p-values, but testing multiple outcomes creates a multiplicity issue. In general, repeated testing increases the chance of at least one apparently positive result unless the analysis plan controls that risk or the results are interpreted appropriately. The registry record does not report a multiplicity adjustment for the posted secondary outcomes. Therefore, their results are best treated as additional descriptive evidence rather than as a set of equally definitive tests.

11. Confidence Intervals and Precision

The primary sponsor-reported estimate is a strata-adjusted percentage difference of 12.2, with a 97.5% confidence interval from 4.6 to 19.8. The entire reported interval is on the positive side of zero. Under the sponsor’s analysis, the range represents values compatible with the data and method at the stated confidence level; it is not a range containing a known fixed treatment effect with certainty.

In general, confidence intervals communicate both the estimated contrast and its precision. The interval width reflects sampling uncertainty under the analysis assumptions. It does not account automatically for possible bias, deviations from the analysis plan, uncertainty about the endpoint’s relevance, or the impact of examining multiple outcomes. The confidence level also does not mean there is a 97.5% probability that the true effect lies in this particular interval.

The sponsor’s adjusted interval should be kept distinct from the unadjusted recalculation. The latter reports a risk-difference estimate of 0.117, while the sponsor reports an adjusted percentage difference and its interval. Differences in adjustment and scale conventions matter when comparing numerical estimates. The registry record does not provide the strata needed to reproduce the sponsor interval from the unadjusted counts alone.

Secondary outcomes also have posted sponsor analyses, including intervals reported at 97.5% for some contrasts. The registry excerpt includes more than one adjusted analysis for some secondary outcomes without enough description to determine the reason for each reported estimate. Those results should not be collapsed into a single interval or treated as independent evidence without understanding their analysis definitions. Precision in an estimate is also separate from certainty about the full clinical meaning of an 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 planning entries are illustrations based on observed results, not the trial’s original design calculation. For the binary outcomes in these entries, the figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect equal to the observed effect or a stated fraction of it. The original trial’s sample-size justification is not reported in the registry record.

The 80% power column describes the planning size associated with an 80% chance of detecting the chosen effect under those assumptions, if that effect and the model assumptions were true. The 90% power column uses a higher target chance of detecting that same chosen effect. Higher target power generally requires more participants, all else equal. For the primary endpoint, the illustrations range from 248 participants per arm for 100% of the observed effect at 80% power to 1,261 participants per arm for 50% of the observed effect at 90% power.

The entries for 75% and 50% of the observed effect show how planning changes when a smaller effect is the target. Smaller effects are harder to distinguish from random variation, so the corresponding planning sizes are larger under the stated assumptions. The curve should be read as another view of this relationship between the chosen effect and planned sample size, not as a result observed in the trial.

These are planning illustrations, not observed power. They do not tell whether the completed trial was adequately designed under its original assumptions, which are not reported in the registry record, and they do not predict the result of another study without the same assumptions.

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 = 0.260; treatment proportion p₁ = 0.377; average p̄ = 0.319.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6591 = 1.2918.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6539 = 0.5503.
4. n = (1.2918 + 0.5503)² / (0.1170)² = 247.8, rounded up to 248 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 <- 0.260377358490566                          # control proportion
p1 <- 0.377394636015326                          # 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(3989349)
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 = 248 (80% power), 332 (90% power)
 75% of observed effect: n per arm = 431 (80% power), 576 (90% power)
 50% of observed effect: n per arm = 943 (80% power), 1,261 (90% power)
power.prop.test: 247.8 
Simulated power at n = 248 per arm: 0.808 (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 registry reports a sponsor analysis using the Cochran-Mantel-Haenszel method for the primary comparison. It gives a strata-adjusted percentage difference of 12.2, a 97.5% confidence interval from 4.6 to 19.8, and p < 0.001. This is the analysis reported by the sponsor, and it incorporates stratification in a way that the simple unadjusted recalculation does not.

The unadjusted recalculation estimates a risk difference of 0.117 from the posted group summary data and reports an unadjusted p-value of 0.001. It is a straightforward check based on the posted summaries, not a reconstruction of the sponsor’s analysis. Since the record does not identify the strata or full model details, the adjusted estimate cannot be independently reproduced from the excerpt.

The results are broadly similar in direction, but the numerical estimates and p-values should not be merged: the sponsor’s is a stratified percentage difference, while the recalculation is unadjusted. The registry record does not mark a discrepancy between them. The sponsor result is therefore best read as the trial’s reported adjusted analysis, with the recalculation serving as a separate descriptive comparison rather than a replacement.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 18 outcome measures and 20 analyses. It does not report whether the study used a formal procedure to control multiplicity across secondary endpoints, populations, time points, or analyses. Without that information, the secondary p-values cannot be interpreted as though only one hypothesis had been tested. In general, testing many hypotheses increases the chance that some results will appear statistically notable by chance; multiplicity procedures can address that issue, but their use and details must be reported to assess their effect.

The primary endpoint is explicitly identified, and the sponsor reports a Cochran-Mantel-Haenszel analysis. However, the full statistical analysis plan and the timing of any analysis decisions are not reported in the registry record. Interim analyses and any associated statistical adjustments are not reported in the registry record. The original sample-size rationale and the specific stratification variables are also not reported in the registry record.

The primary endpoint rules do address missing Week 16 observations: participants with missing data were classified as non-responders. The record also says data after rescue therapy were treated as treatment failure. These definitions should be considered when interpreting the response percentages. The registry excerpt does not report the amount or pattern of missing data, sensitivity analyses under alternative assumptions, or additional analyses of rescue therapy.

The primary population is the intent-to-treat population, defined as all randomized participants. This definition supports an assignment-based comparison, but the record excerpt does not give a complete account of adherence, discontinuation, or other post-randomization events. The information available is therefore insufficient to evaluate whether alternative missing-data assumptions, analysis populations, or multiplicity adjustments would materially change the reported estimates.

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: endometriosis (1.3%), pulmonary embolism (1.3%), duodenal ulcer haemorrhage (1.3%), gastroenteritis (1.3%), comminuted fracture (1.3%).

For the initial treatment period, the registry lists serious adverse events in 13 participants among 519 at risk in the nemolizumab group and 3 among 263 at risk in the placebo group. Other adverse events were recorded in 71 among 519 at risk for nemolizumab and 40 among 263 at risk for placebo. The registry lists no deaths in either initial-period group.

These are descriptive counts with their listed at-risk denominators. They do not establish that an event was caused by treatment, and the counts alone do not account for differences in exposure time or event severity beyond the serious-event classification. The record also lists maintenance-period safety groups with different treatment histories: serious events were recorded in 6 among 79, 0 among 77, 2 among 77, and 1 among 84, respectively; no deaths were listed in those groups. These later groups are not a simple continuation of the initial randomized comparison.

The serious-event terms listed in the record include endometriosis, pulmonary embolism, duodenal ulcer haemorrhage, gastroenteritis, comminuted fracture, and intervertebral disc protrusion, each reported as 1.3%. The registry excerpt does not provide enough detail to attribute any event to a treatment or to compare risks causally.

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

The primary result describes the proportion of participants who met a defined investigator-assessed success criterion at Week 16. The posted proportion was 37.7% for nemolizumab and 26.0% for placebo. The sponsor’s adjusted estimate was positive, and its reported confidence interval did not include zero. These results provide evidence of a difference between the randomized groups for this endpoint under the reported analysis.

That statement is narrower than saying that every participant experienced improvement, that all symptoms changed in the same way, or that the result applies to every person with atopic dermatitis. The endpoint required both a specified Week 16 IGA score and a specified improvement from baseline. It also incorporated rules classifying post-rescue data and missing Week 16 data as failures. The posted percentage is thus a result under those operational definitions.

Statistical evidence of a group difference does not establish its clinical importance. The registry record does not report a threshold for a clinically important difference in IGA success, nor does the primary result describe how individual participants valued changes in symptoms or daily functioning. The secondary outcomes offer additional perspectives on itch and sleep, but they have different definitions and multiplicity considerations.

The result also does not answer questions outside the reported comparison, including longer-term effectiveness of the initial-period assignment, rare or delayed harms, or outcomes in populations not represented by the trial. Safety counts are descriptive, and no causal conclusions about individual adverse events follow from those counts alone. The trial supports an endpoint-specific statistical interpretation; broader claims require evidence and information beyond the registry record.

18. Why This Trial Matters Statistically

Several statistical features make this trial useful to examine. It reports a randomized, masked, parallel-group comparison with an active treatment arm and a placebo arm, and it identifies a primary binary endpoint at a defined time point. Those features allow the central result to be expressed as a comparison of response proportions rather than as a within-group change alone.

The primary endpoint also illustrates how an outcome definition shapes an estimate. Success required a final IGA score and improvement from baseline, while rescue therapy and missing Week 16 observations were assigned failure status. A response percentage cannot be understood fully without those rules. The same principle applies to secondary symptom measures: their thresholds, assessment populations, and analysis definitions determine what their percentages represent.

The record provides both a sponsor-reported stratified analysis and enough summary information for an unadjusted recalculation. Their related but non-identical estimates show why an adjusted analysis should not be treated as a simple restatement of crude arm percentages. The sponsor’s adjustment method is named, while its strata and detailed model are not reported, which demonstrates the importance of complete statistical reporting for reproducibility.

Finally, the planning illustrations make the dependence of sample-size requirements on effect assumptions visible. Planning for a smaller effect requires more participants under the stated assumptions. These calculations are not observed power and do not substitute for the trial’s original design rationale, which is not reported. Together, the endpoint rules, adjusted and unadjusted analyses, precision estimates, multiplicity concerns, and safety counts offer a compact example of how to read a registry result without overextending its conclusions.

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 excerpt does not identify the strata used in the sponsor’s Cochran-Mantel-Haenszel analysis or give enough detail to reproduce that adjusted result. The full statistical analysis plan, original sample-size justification, and any interim-analysis procedures are not reported in the registry record. This limits assessment of prespecification and of the analysis choices underlying the posted estimates.

The record lists 18 outcome measures and 20 analyses, but a multiplicity strategy is not reported. Some secondary outcomes include more than one sponsor-reported adjusted estimate without enough explanation of the distinctions. This makes it difficult to determine the intended hierarchy among secondary findings or how their inferential strength should be calibrated.

Missing Week 16 primary endpoint data and post-rescue observations were handled as failures according to the endpoint definition. The registry excerpt does not report the amount or pattern of missingness, or sensitivity analyses using alternative assumptions. The result is therefore interpretable under the stated rule, but robustness to other plausible missing-data approaches cannot be assessed from this record.

The safety information is presented as counts among listed at-risk participants. The excerpt does not include exposure-adjusted event rates, detailed event timing, or enough clinical context to determine causality. Maintenance-period groups have different prior treatment assignments and sizes, so their counts do not represent a direct comparison equivalent to the initial-period randomized groups.

Finally, the primary outcome is limited to an investigator-assessed response at Week 16. The record does not provide a clinically important difference threshold or establish how the endpoint relates to longer-term outcomes. These limits do not erase the reported result, but they define the scope of conclusions that can be drawn from the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy & Safety of Nemolizumab in Subjects With Moderate-to-Severe Atopic Dermatitis — NCT03989349.
• Registry record last updated 2024-08-14; status last verified 2024-08.
• Results first posted 2024-08-14.
• 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

NCT03989349 is a completed Phase 3 randomized, quadruple-masked, parallel-group, placebo-controlled study sponsored by Galderma R&D. It enrolled adults and adolescents with moderate-to-severe atopic dermatitis not adequately controlled with topical treatments. Nemolizumab 30 mg and placebo were administered by subcutaneous injection during the initial treatment period.

The primary endpoint was IGA success at Week 16 in the intent-to-treat population. The posted proportions were 37.7% with nemolizumab and 26.0% with placebo. The sponsor reported a strata-adjusted percentage difference of 12.2, with a 97.5% confidence interval from 4.6 to 19.8 and p < 0.001. Secondary outcomes primarily covered itch and sleep measures. Safety results are descriptive, and the registry excerpt does not report the multiplicity strategy, original sample-size justification, or detailed adjustment strata.