Efficacy and Safety of QGE031 (Ligelizumab) in Patients With Peanut Allergy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of QGE031 (Ligelizumab) in Patients With Peanut Allergy (NCT04984876), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Tolerated a Single Dose of >= 600 mg (1044 mg Cumulative Tolerated Dose) of Peanut Protein Without Dose-limiting Symptoms at Week 12.

2. Clinical Question

3. Trial Design

The registry describes NCT04984876 as a Phase 3, multicenter, randomized, double-blind, placebo-controlled, parallel-group study of ligelizumab in participants with peanut allergy. Masking is recorded as triple. The study’s official title describes a 52-week assessment of clinical efficacy and safety; the brief summary identifies subcutaneous ligelizumab regimens of 240 mg and 120 mg every four weeks. Enrollment is recorded as 211.

The listed treatment arms include ligelizumab 120 mg or 240 mg throughout the treatment period, as well as groups that began with placebo and later received ligelizumab. In the staged regimens, placebo was given for the first 8 or 16 weeks, followed by ligelizumab for the remainder of the described treatment period. For the primary outcome, the registry identifies the 120 mg and 240 mg arms and the placebo-to-ligelizumab arm labelled as placebo for efficacy estimands. The posted primary counts compare each active-dose group with the placebo comparator; they do not establish a direct comparison between the two active doses.

The study start is recorded as 2021-12-07 and primary completion as 2023-11-27. The current status in the registry record is terminated. The reason for termination, the number who completed follow-up, and the relationship between termination and the planned treatment schedule are not reported in the registry record. The original design’s sample-size justification, allocation ratio, detailed analysis plan and any interim-analysis plan are also 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS). This outcome measure applies to ligelizumab 120 mg arm, ligelizumab 240 mg arm, and placebo 16-week to ligelizumab 120/240 mg arm (labelled as placebo for efficacy estimands).

5. Baseline Characteristics

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

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Tolerated a Single Dose of >= 600 mg (1044 mg Cumulative Tolerated Dose) of Peanut Protein Without Dose-limiting Symptoms at Week 12, measured over Week 12.

The primary endpoint is the percentage of participants who tolerated a single dose of >= 600 mg of peanut protein without dose-limiting symptoms at Week 12. The registry also expresses that threshold as a cumulative tolerated dose of 1044 mg. Cumulative tolerated dose is defined as the sum of tolerated doses and does not include the dose that caused a reaction. The assessment took place during a double-blind placebo-controlled food challenge.

A dose-limiting symptom was defined as a true allergic reaction during administration of a single peanut-protein dose that, in the investigator’s view, should prevent further doses. Symptoms requiring rescue medication also counted as dose-limiting. This definition makes the endpoint a threshold-based responder outcome: each participant is classified according to whether the specified challenge dose was tolerated under the study criteria.

This type of endpoint is used to summarize challenge performance in a clinically defined form rather than only reporting a continuous dose measurement. The responder rate can be compared between randomized groups, while the threshold makes clear what level of challenge tolerance counts as a response. The endpoint does not describe all symptoms, all exposures, or experiences outside the food challenge. The registry’s stated rule also classified participants as non-responders if they discontinued treatment or missed more than 1 doses before Week 12 for reasons other than operational complications caused by a public health emergency.

7. Results Posted in the Registry

• Ligelizumab 240 mg: 44.7% (21/47) versus 4.3% (1/23) on control; risk difference 40.3 percentage points (95% CI 23.9 to 56.8), risk ratio 10.28 (1.47–71.73); unadjusted two-proportion z-test p = <0.001.
• Ligelizumab 120 mg: 15.7% (8/51) versus 4.3% (1/23) on control; risk difference 11.3 percentage points (95% CI -1.7 to 24.3), risk ratio 3.61 (0.48–27.19); unadjusted two-proportion z-test p = 0.167.

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 Who Tolerated a Single Dose of >= 1000 mg (2044 mg Cumulative Tolerated Dose) of Peanut Protein Without Dose-limiting Symptoms at Week 12

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ligelizumab 240 mg: 29.8% (14/47) versus 4.3% (1/23) on control; risk difference 25.4 percentage points (95% CI 9.9 to 40.9), risk ratio 6.85 (0.96–48.95); unadjusted two-proportion z-test p = 0.015.
  • Ligelizumab 120 mg: 11.8% (6/51) versus 4.3% (1/23) on control; risk difference 7.4 percentage points (95% CI -4.7 to 19.6), risk ratio 2.71 (0.35–21.21); unadjusted two-proportion z-test p = 0.313.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Ligelizumab 240 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ligelizumab 120 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Tolerated a Single Dose of 3000 mg (5044 mg Cumulative Tolerated Dose) of Peanut Protein Without Dose-limiting Symptoms at Week 12

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ligelizumab 240 mg: 14.9% (7/47) versus 4.3% (1/23) on control; risk difference 10.5 percentage points (95% CI -2.6 to 23.7), risk ratio 3.43 (0.45–26.21); unadjusted two-proportion z-test p = 0.193.
  • Ligelizumab 120 mg: 9.8% (5/51) versus 4.3% (1/23) on control; risk difference 5.5 percentage points (95% CI -6.2 to 17.1), risk ratio 2.25 (0.28–18.23); unadjusted two-proportion z-test p = 0.426.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ligelizumab 240 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ligelizumab 120 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Tolerated a Single Dose of >= 1000 mg (2044 mg Cumulative Tolerated Dose) of Peanut Protein Without Dose-limiting Symptoms at Week 12 After 4 Weeks of Treatment

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Placebo 8 Weeks and Ligelizumab 120 mg: 2.3% (1/44) versus 17.4% (8/46) on control; risk difference -15.1 percentage points (95% CI -26.9 to -3.3), risk ratio 0.13 (0.02–1.00); unadjusted two-proportion z-test p = 0.017.
  • Placebo: 4.3% (1/23) versus 17.4% (8/46) on control; risk difference -13.0 percentage points (95% CI -26.8 to 0.7), risk ratio 0.25 (0.03–1.88); unadjusted two-proportion z-test p = 0.129.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Placebo 8 Weeks and Ligelizumab 120 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Placebo and the control. The interval gives the range of effects that remain compatible with the data.

Across the posted Week 12 secondary challenge outcomes, the broad pattern is that the number meeting the more demanding tolerance thresholds is smaller than for the primary threshold. The comparisons do not all point to equally clear differences, and the pattern varies across doses and outcome definitions. Other secondary measures extend the assessment to later challenge tolerance, maximum symptom severity, changes in maximum tolerated dose, and peanut-specific IgE and IgG4.

These outcomes add context to the primary responder result by considering different challenge thresholds, timing and laboratory measures. They do not constitute a single, interchangeable measure of treatment response. A result for one threshold does not establish the same effect at another threshold or on a biomarker, and the secondary outcomes should be interpreted according to their separate definitions and analysis populations. The registry posts 14 secondary outcomes, but detailed results are not available for every listed measure in the record described.

Unadjusted secondary findings carry less weight when many outcomes and comparisons are examined. The chance of seeing a seemingly notable result can increase across multiple tests, even when each individual test uses a conventional significance threshold. The registry record does not report a multiplicity-control procedure for the secondary results. Consequently, isolated secondary p-values should be treated as exploratory unless the analysis plan establishes otherwise; such a plan is not reported in the registry record.

The overall secondary pattern can be considered alongside the primary endpoint, but it should not be used to resolve uncertainty in the primary analysis or to imply a broad conclusion across outcomes. The trial’s terminated status and the absence of full reporting for all listed secondary endpoints further limit how comprehensively the full outcome pattern can be assessed.

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

• Percentage of Participants Who Tolerated a Single Dose of >= 1000 mg (2044 mg Cumulative Tolerated Dose) of Peanut Protein Without Dose-limiting Symptoms at Week 12
• Percentage of Participants Who Tolerated a Single Dose of 3000 mg (5044 mg Cumulative Tolerated Dose) of Peanut Protein Without Dose-limiting Symptoms at Week 12
• Percentage of Maximum Severity of Symptoms Occurring at Any Challenge Dose of Peanut Protein up to and Including 1000 mg at Week 12
• Percentage of Participants Who Tolerated a Single Dose of >= 1000 mg (2044 mg Cumulative Tolerated Dose) of Peanut Protein Without Dose-limiting Symptoms at Week 12 After 4 Weeks of Treatment
• Percentage of Participants Who Tolerated the Specified Peanut Protein Dose Without Dose-limiting Symptoms at Week 52
• Change From Baseline in Maximum Tolerated Dose (MTD) of Peanut Protein Without Dose-limiting Symptoms During the DBPCFC at Week 12 and Week 52
• Change From Baseline in Peanut-specific Immunoglobulin E (IgE) at Week 12 and Week 52
• Change From Baseline in Peanut-specific Immunoglobulin G4 (IgG4) at Week 12 and Week 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: a participant either met the Week 12 tolerance threshold without dose-limiting symptoms or did not. The registry posts counts by group. A useful way to compare binary outcomes is the risk difference, which subtracts the observed proportion in the comparator group from the observed proportion in the active-treatment group. A positive difference means the observed responder proportion was higher in the active group; a negative difference means it was lower. The recalculated differences are unadjusted and use the posted summary counts.

What does an unadjusted comparison tell the reader?

An unadjusted comparison describes the observed groups without accounting for other variables through a regression model. Random assignment is intended to create comparable groups, but an unadjusted estimate is still a summary of the observed data. It does not establish that every prognostic factor was balanced, and the posted counts do not allow those factors to be examined. The record’s stated analysis population and missing-response rule also matter when interpreting the counts.

The registry’s sponsor-reported primary analyses use logistic regression and report odds ratios. An odds ratio compares the odds of response between groups, rather than subtracting the probabilities. Odds ratios and risk differences answer related but distinct questions, and their numerical values are not directly comparable. The registry record does not report the full regression specification or covariates, so the extent and details of adjustment are not reported in the registry record. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence over the simple unadjusted recalculation.

How should the p-values be read?

A p-value describes how compatible the observed data are with a specified null model, under the assumptions of the analysis. A small p-value is not the probability that the null hypothesis is true, nor does it measure the clinical importance of an effect. The unadjusted p-values accompanying recalculated risk differences are not the same as the p-values from the sponsor’s logistic-regression analyses. They arise from different analyses and may differ for that reason as well as because of the discrepancy noted in the registry record. No multiplicity adjustment is described in the posted results.

For the primary outcome, the sponsor reports a p-value of 0.002 for the 240 mg comparison and 0.073 for the 120 mg comparison. The associated intervals show substantial uncertainty in the estimated odds ratios. In general, a result should be read using its effect estimate and interval as well as its p-value. A threshold-based distinction between p-values does not itself show that the two dose effects differ from each other; a direct dose-to-dose comparison is not reported.

Why do sparse counts matter?

When events are uncommon, each observed response has a relatively large influence on the estimated group contrast. This can make estimates unstable and intervals wide. Logistic regression can also produce imprecise odds-ratio estimates when event counts are limited. That is relevant to these results because the posted responder counts are small, particularly in the placebo group. The sponsor’s broad confidence intervals reflect limited precision in the effect estimates, even where a reported p-value is small.

General statistical explanation: a confidence interval describes a range of values reasonably compatible with the data and the method used to calculate it. It is not a guarantee that the true value lies within the interval, and it does not include every possible source of uncertainty. Here, uncertainty also concerns the study’s terminated status, details of the analysis that are not reported, and the applicability of a food-challenge response to outcomes not measured by this endpoint.

What is and is not described about the analysis?

The record identifies the Full Analysis Set for the primary outcome and gives a specific non-responder rule for treatment discontinuation or missing more than 1 doses before Week 12, with an exception for operational complications caused by a public health emergency. It does not provide further details on other missing-data handling, sensitivity analyses, the model specification, or adjustments for multiple comparisons. Those features are not reported in the registry record and should not be inferred from the posted estimates.

The sample-size figures are planning illustrations based on the observed effect, not a reconstruction of the original trial design. They use the assumptions stated in the sample-size material. They do not explain the study’s actual enrollment target or provide observed power. Interpretation of the observed trial results should remain separate from those hypothetical planning calculations.

11. Confidence Intervals and Precision

The confidence intervals show how much uncertainty surrounds the estimated comparisons under the stated calculation method. For the unadjusted primary risk difference comparing 240 mg with placebo, the 95% interval is 0.239 to 0.568. It does not include zero, the value corresponding to no difference in responder proportions. For the 120 mg comparison, the interval is -0.017 to 0.243 and includes zero. This means the posted counts are compatible with a range of values that includes no difference as well as positive differences.

The sponsor’s reported odds-ratio intervals are much wider: 4.34 to 506.78 for 240 mg and 0.80 to 100.98 for 120 mg. The breadth indicates limited precision in the odds-ratio estimates. The interval for 120 mg includes the value 1, which represents equal odds in the groups, while the 240 mg interval does not. These sponsor analyses take precedence over the unadjusted recalculations because the registry record identifies a discrepancy. The risk-difference intervals and odds-ratio intervals use different effect scales and should be interpreted separately.

General statistical explanation: a confidence interval reflects sampling uncertainty under the analysis method; it is not a range of outcomes for individual participants and does not account automatically for every design or reporting limitation. Sparse event counts tend to make intervals wider, and a small comparator group can contribute to imprecision. The posted counts and wide sponsor intervals warrant caution about the exact magnitude of the association, even when the direction of the estimate is clear.

The intervals do not resolve questions about the termination, unreported analysis details, missing data beyond the stated rule, or the effects of multiple testing. Nor do they establish whether ligelizumab doses differ from one another. The posted primary analyses compare each dose with placebo.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the original trial’s documented design assumptions. For these binary outcomes, the figures are participants per arm, rather than total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to be detected is a stated fraction of the observed effect. The original trial’s own sample-size assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm estimated to be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect and the other assumptions were true. The 90% power column gives the corresponding planning number for a higher chance of detection. These are design calculations for hypothetical future studies, not a measure of the evidential strength of the completed trial.

Each row considers a different fraction of the observed effect. Planning for 75% or 50% of the observed effect represents a smaller effect to detect than planning for 100% of it. Smaller effects generally require more participants to distinguish them from random variation under otherwise similar assumptions. The figures can therefore be used to understand how the assumed effect size influences planning, not as a recommended enrollment target for a future study without further design work.

This is not observed power. Observed power is not a useful substitute for reading the effect estimate, confidence interval and study limitations after results are known. The original trial’s design rationale, including the reason for its enrollment target, is not reported in the registry record.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.043; treatment proportion p₁ = 0.447; average p̄ = 0.245.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6084 = 1.1924.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5374 = 0.4523.
4. n = (1.1924 + 0.4523)² / (0.4033)² = 16.6, rounded up to 17 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 <- 0.0434782608695652                          # control proportion
p1 <- 0.446808510638298                          # 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(4984876)
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 = 17 (80% power), 22 (90% power)
 75% of observed effect: n per arm = 26 (80% power), 34 (90% power)
 50% of observed effect: n per arm = 47 (80% power), 62 (90% power)
power.prop.test: 16.6 
Simulated power at n = 17 per arm: 0.843 (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 sponsor analyses using logistic regression. For the primary comparison of ligelizumab 240 mg with placebo, the reported odds ratio is 25.83, with a 95% confidence interval of 4.34 to 506.78 and p = 0.002. For 120 mg versus placebo, the reported odds ratio is 5.10, with a 95% confidence interval of 0.80 to 100.98 and p = 0.073.

The recalculated results use the posted group counts to estimate unadjusted risk differences and p-values. They are not the same estimand or model as the sponsor’s logistic-regression odds ratios. The registry record flags a discrepancy between the recalculated and reported analyses, so the sponsor’s own analysis takes precedence. The recalculation can still help describe the observed responder proportions and their unadjusted contrasts, but it should not replace the reported sponsor analysis.

The registry does not report enough detail to reconstruct the sponsor’s full model or determine the source of the discrepancy. Covariates, model specification, and any additional analysis details beyond the reported method are not reported in the registry record. The sponsor’s intervals are broad, so the point estimates should not be treated as precise measures of the size of the effect. The reported comparisons are each against placebo; they do not directly test whether the two ligelizumab doses differ.

15. Multiplicity, Missing Data and Analysis Populations

The record identifies the Full Analysis Set for the primary endpoint and defines a non-responder rule for participants who discontinued treatment or missed more than 1 doses before Week 12 for reasons other than operational complications caused by a public health emergency. This gives some information about how particular cases were classified for the primary outcome. The registry record does not report a fuller account of missing-data methods, the number of missing Week 12 assessments, sensitivity analyses, or whether other missing observations were handled differently.

The primary endpoint has two active-dose comparisons against placebo, and the registry lists numerous secondary outcomes. Testing several hypotheses can increase the chance of at least one apparently notable result arising by chance. The posted record does not report whether a family-wise error procedure, hierarchical testing strategy, or other multiplicity adjustment was used. The protocol’s and statistical analysis plan’s multiplicity approach is not reported in the registry record. Without that information, unadjusted secondary results should be viewed cautiously, and the nominal p-values should not be treated as if they necessarily control the overall false-positive risk.

The sponsor’s primary analyses are reported as logistic regression, but the model specification and covariates are not reported in the registry record. The reason for the discrepancy between the reported analyses and the unadjusted recalculations is also not reported. No interim-analysis plan, stopping rule, or original sample-size justification is reported in the registry record. The record’s terminated status does not explain whether stopping affected enrollment, follow-up, or the analysis set.

These gaps do not invalidate the results that are posted, but they limit independent assessment of how robustly the analysis addressed missingness, multiplicity and model choices. Interpretation should distinguish what the record explicitly states—the endpoint definition, the primary analysis population and the stated non-responder rule—from analysis details that remain unreported.

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: post procedural complication (1.0%).

The safety record separates serious adverse events from other adverse events and reports groups for different exposure periods. In the placebo-controlled period up to Week 8, no serious adverse events were reported in the listed ligelizumab 240 mg, ligelizumab 120 mg or placebo groups. The corresponding other-adverse-event counts were 21, 17 and 27. For the placebo-controlled period up to Week 16, no serious adverse events were reported in the listed active-dose groups or placebo group; other-adverse-event counts were 26, 20 and 9.

For the broader exposure categories reported up to Week 68, no serious adverse events were reported in the 240 mg group, while 1 was reported in the 120 mg group. No deaths were reported in the listed safety groups. The registry identifies “Post procedural complication” as a top serious-event term, at 1.0%.

These are descriptive counts across groups and periods, not adjusted comparisons of safety risk. The categories cover different exposure windows and may not be mutually exclusive; counts should not be added across periods or groups. The record does not provide enough information to assess event timing, causality, severity for all other events, or the impact of termination on safety follow-up. Absence of a reported serious event in a group does not establish absence of risk.

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

The posted primary outcome describes whether participants met a defined peanut-protein challenge threshold at Week 12. In the observed data, more participants in the 240 mg arm met that threshold than in placebo, while the estimate for 120 mg was less precise and its confidence interval included no difference. The sponsor’s own logistic-regression analyses take precedence over the unadjusted recalculations because the registry record flags a discrepancy. Those sponsor results also have broad confidence intervals, so the exact magnitude remains uncertain.

This result does not establish that either regimen changes a participant’s everyday experience of peanut exposure. The endpoint was measured during a controlled food challenge, using a particular dose threshold and a specified definition of dose-limiting symptoms. It does not answer questions about all possible doses, symptoms outside the challenge, long-term outcomes, or outcomes not recorded in the registry.

The primary comparisons are each against placebo. They do not show whether the 240 mg dose is better than the 120 mg dose, because a direct dose-to-dose analysis is not reported. The registry’s other listed outcomes may add context, but their multiplicity handling and complete result pattern are not reported in the registry record.

The record marks the study terminated but does not state why. The reason for termination, its effect on follow-up and the completeness of all planned analyses are not reported in the registry record. The results therefore need to be understood within the limits of the posted Week 12 findings, group sizes, sparse responder counts, uncertainty intervals and incomplete reporting of some analysis details. They describe the data recorded for this trial; they do not provide a complete answer to every question about ligelizumab, peanut allergy or longer-term safety.

18. Why This Trial Matters Statistically

This trial illustrates several important statistical issues in clinical research. First, a binary responder outcome can be easy to communicate because it ties the result to a defined threshold, but the choice of threshold matters. The primary endpoint concerns tolerance of a single challenge dose of >= 600 mg and a cumulative tolerated dose of 1044 mg. Secondary thresholds and other challenge measures ask related but distinct questions.

Second, the observed responder counts are limited, particularly in the placebo group. Sparse counts make effect estimates sensitive to individual outcomes and can produce wide intervals. The sponsor’s odds-ratio intervals make that imprecision visible: the estimated association is not known with the same precision as the point estimate alone might suggest. Reporting both the estimate and its interval is therefore central to interpreting the result.

Third, the record juxtaposes sponsor-reported logistic-regression analyses with simple unadjusted recalculations that do not agree exactly. The registry flags the discrepancy, and the sponsor’s analysis takes precedence. This is a useful reminder that analysis method and estimand matter: an odds ratio from a regression model is not equivalent to a crude risk difference from group counts.

Finally, multiple outcomes, a terminated status and incomplete reporting of analysis details shape the strength of conclusions. The record gives enough information to describe the primary endpoint and several posted results, but does not report the original sample-size rationale, multiplicity plan or reason for termination. Statistical interpretation must account for both the numbers reported and the limits of the record.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record marks the trial terminated, but the reason is not reported. It is therefore not possible from the record to determine whether termination affected planned enrollment, treatment exposure, follow-up completeness or the timing of analyses. Although the study title describes a 52-week assessment, the primary endpoint is a Week 12 food-challenge result; the later study period should not be assumed to be fully represented by that endpoint.

The primary responder counts are small, including only 1 responder in the placebo group. This contributes to broad uncertainty, especially for odds-ratio estimates. The record’s reported primary analyses and the unadjusted recalculations differ, and the full model specification needed to independently reproduce the sponsor analysis is not reported. The sponsor analysis takes precedence, but the source of the discrepancy is not reported in the registry record.

The endpoint is specific to a controlled food challenge and a defined dose threshold. It does not encompass all clinically relevant outcomes or exposures. The primary comparisons do not directly compare the two active doses. Although the registry lists several secondary outcomes, the multiplicity approach and detailed results for every listed outcome are not reported. Missing-data handling beyond the stated primary non-responder rule, the number of missing observations and sensitivity analyses are also not reported in the registry record.

Safety counts are presented across multiple exposure periods and categories. They are descriptive and do not, by themselves, establish comparative safety. The record does not explain the relationship between overlapping exposure groups, or give full event-level detail in the information posted. These limitations constrain interpretation of the size, generality and completeness of the findings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of QGE031 (Ligelizumab) in Patients With Peanut Allergy — NCT04984876.
• Registry record last updated 2025-04-29; status last verified 2025-04.
• Results first posted 2024-10-08.
• 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

NCT04984876 is a terminated Phase 3 randomized, double-blind, placebo-controlled, parallel-group study of ligelizumab in participants with medically confirmed IgE-mediated peanut allergy. The primary Week 12 endpoint assessed tolerance of a single peanut-protein dose of >= 600 mg without dose-limiting symptoms during a controlled food challenge. The posted counts were 21 of 47 for ligelizumab 240 mg, 8 of 51 for 120 mg and 1 of 23 for placebo.

The sponsor reported logistic-regression odds ratios for each active dose versus placebo. The registry record flags a discrepancy with simple unadjusted recalculations, so the sponsor’s analysis takes precedence. Confidence intervals are broad, and the 120 mg estimate is particularly uncertain. Secondary outcomes cover additional challenge thresholds and other measures; the multiplicity approach is not reported. The reason for termination and several analysis details are not reported in the registry record.