Efficacy and Safety of Erenumab in Pediatric Subjects With Chronic Migraine: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Erenumab in Pediatric Subjects With Chronic Migraine (NCT03832998), a randomized phase 3 study. The primary outcome is Change From Baseline in MMD to Week 9 Through Week 12 (Month 3) of the DBTP.

2. Clinical Question

The registry record describes a pediatric chronic migraine prevention study, but its prespecified primary efficacy results are only for adolescents. The primary outcome counts monthly migraine days, with baseline defined from the four-week baseline phase and the Month 3 assessment covering Week 9 through Week 12. The result therefore addresses a specific age group and assessment period, not all pediatric participants or all follow-up periods. The record also lists outcomes concerning monthly headache days, a reduction threshold for migraine days, migraine attack severity, and migraine-related disability and productivity. Those outcomes address related but distinct aspects of migraine and do not replace the primary comparison.

3. Trial Design

This was a Phase 3, randomized, quadruple-masked, parallel-group, placebo-controlled study sponsored by Amgen. The registry record lists an enrollment of 284 and a status of completed. The recorded study start was 2019-09-05, and primary completion was 2025-01-08. The study included children aged 6 to < 12 years and adolescents aged 12 to < 18 years with chronic migraine.

Participants were assigned to erenumab dose groups or placebo. For the dose levels described in the record, assignment was to one of two doses determined by body weight at Day 1. The record distinguishes participants enrolled under the original protocol or protocol amendment 1 from those enrolled under protocol amendment 2, but does not give further detail about how those protocol groups affect interpretation of the primary result. The posted primary analysis compares the combined adolescent erenumab group with adolescent placebo, rather than reporting a separate primary comparison for each dose level.

The primary efficacy population is narrower than the full enrolled population. It consists of randomized adolescent participants with data available during Month 3. The reported arm sizes for the primary endpoint are 118 for placebo and 124 for erenumab. Safety counts use different at-risk totals, so those counts should not be mistaken for the primary endpoint analysis denominators.

The registry record reports the primary analysis method as a linear mixed effects repeated measures model and identifies a 95% confidence interval for the treatment contrast. It does not report the original sample-size justification, detailed handling of missing outcome data, or whether interim efficacy analyses were planned or conducted. The randomization and masking labels describe the general design; further procedural details 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: As pre-specified in the statistical analysis plan (SAP) and protocol, all DBTP summaries were based on the primary analysis, performed on a locked database when the last adolescent participant completed DBTP assessments, to assess combined AMG 334 doses versus placebo during DBTP. At the time of primary analysis, AMG 334 dose levels remained blinded. Per the SAP, DBTP assessments were not repeated at final analysis; any dose-level DBTP summaries were exploratory in nature.

Only the first 6 of 10 groups are shown.

DBTP Period

Reasons for not completing this period:

DLBEP Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set: all adolescent participants who were randomized in the trial and had data available during Month 3.

5. Baseline Characteristics

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

Population: Full analysis set: all participants who were randomized in the trial.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in MMD to Week 9 Through Week 12 (Month 3) of the DBTP, measured over Baseline to Week 12.

The primary endpoint is change from baseline in monthly migraine days (MMD) to Week 9 through Week 12, described as Month 3 of the double-blind treatment phase. A migraine day was defined as a calendar day on which a participant developed a qualified migraine headache, including onset, continuation, or recurrence. Baseline MMD was the number of migraine days in the four-week baseline phase; MMD during treatment was counted between monthly investigational product doses.

This endpoint expresses the change in migraine-day frequency over a defined period, rather than simply the number of attacks or the presence of a particular symptom. Comparing change from baseline helps describe how each randomized group’s outcome shifted from its baseline level. The registry reports least squares means, which are model-adjusted group estimates, and a difference in those estimates for erenumab versus placebo.

The endpoint is useful for the stated trial question because it directly measures the frequency outcome the study hypothesis concerns. It is nonetheless a time-specific measure: the primary result concerns Month 3, not a long-term average or every month of follow-up. The reported primary analysis also applies to adolescents with Month 3 data, not to the entire pediatric population. Other listed measures, including headache days, responder status, attack severity, and disability, capture related but non-identical outcomes.

7. Results Posted in the Registry

• Adolescents - AMG 334 (DBTP): mean -4.53 versus -4.45 on control; difference -0.08 (95% CI -1.81 to 1.65), standardized effect d = -0.01; z-test p = 0.928.

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.

Change From Baseline in Monthly Headache Days to Week 9 Through Week 12 (Month 3) of the DBTP

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Adolescents - AMG 334 (DBTP): mean -5.02 versus -4.52 on control; difference -0.50 (95% CI -2.12 to 1.12), standardized effect d = -0.08; z-test p = 0.546.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Adolescents - AMG 334 (DBTP) and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With at Least 50% Reduction in MMD From Baseline to Week 9 Through Week 12 (Month 3) of the DBTP

• 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:
  • Adolescents - AMG 334 (DBTP): 24.2% (32/132) versus 29.5% (38/129) on control; risk difference -5.2 percentage points (95% CI -16.0 to 5.5), risk ratio 0.82 (0.55–1.23); unadjusted two-proportion z-test p = 0.342.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Adolescents - AMG 334 (DBTP) and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in MMD to the Average of the First 3 Months (Week 1 Through Week 12) of the DBTP

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Adolescents - AMG 334 (DBTP): mean -3.48 versus -3.53 on control; difference 0.05 (95% CI -1.35 to 1.45), standardized effect d = 0.01; z-test p = 0.944.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Adolescents - AMG 334 (DBTP) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several related dimensions: monthly headache days, a responder threshold based on reduction in monthly migraine days, the average of the first three months, migraine attack severity, and migraine-related disability and productivity. These outcomes broaden the clinical description beyond the primary Month 3 migraine-day change, but they do not measure the same construct or necessarily use the same analysis population.

The numerical secondary results available for adolescents do not form a clear pattern of separation from placebo. The reported continuous contrasts have confidence intervals spanning zero, while the reported responder odds-ratio interval spans 1. This general pattern is consistent with the primary result in that the available comparisons do not precisely distinguish the groups. It should not be taken as proof that all outcomes are identical or that no potentially meaningful difference exists.

The registry record identifies five secondary outcomes, while detailed numerical comparisons are available for a subset of them. Results for the listed monthly average severity and PedMIDAS outcomes are not reported in the registry record. As a result, the full secondary outcome profile cannot be assessed from the results.

Secondary results generally carry less confirmatory weight than a prespecified primary endpoint, especially when several outcomes are considered. Testing multiple outcomes increases the opportunity for chance findings if no multiplicity procedure is used. The registry record does not report a multiplicity adjustment for these secondary comparisons. Their estimates can still be informative as supporting or exploratory evidence, but isolated secondary findings should not be treated as definitive without the planned testing framework and complete results.

The secondary measures also have differing denominators, and the record does not give all analysis-method details or p-values for each comparison. Interpretation should therefore focus on the broad direction and uncertainty of the available results, rather than selecting one outcome as decisive.

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

• Change From Baseline in Monthly Headache Days to Week 9 Through Week 12 (Month 3) of the DBTP
• Number of Participants With at Least 50% Reduction in MMD From Baseline to Week 9 Through Week 12 (Month 3) of the DBTP
• Change From Baseline in MMD to the Average of the First 3 Months (Week 1 Through Week 12) of the DBTP
• Change From Baseline in Monthly Average Severity of Migraine Attacks to Week 9 Through Week 12 (Month 3) of the DBTP
• Change From Baseline in Migraine-related Disability and Productivity as Measured by the Modified Pediatric Migraine Disability Assessment (PedMIDAS) to Week 9 Through Week 12 (Month 3) of the DBTP

9. Statistical Interpretation

10. Statistical Methods Explained

The registry identifies the primary method as a linear mixed effects repeated measures model. In general, this class of model analyzes repeated measurements while accounting for the fact that observations from the same participant are related. Rather than treating each measurement as entirely independent, the model can represent participant-level variation and estimate group patterns across scheduled visits. The registry states that participants were included as a random effect.

What does the model adjust for?

The stated model included treatment group, baseline value as a covariate, region and prior preventive treatment failure as stratification factors, scheduled visit, and the interaction between treatment group and scheduled visit. In general, including baseline as a covariate can account for baseline differences when estimating follow-up outcomes. Including scheduled visit and its interaction with treatment group allows the estimated treatment contrast to vary by visit. The registry does not provide coefficient estimates for these model terms or further detail on their coding.

The primary group estimates are least squares means (LSMs). In general, an LSM is a model-based estimate adjusted for the variables in the analysis, rather than a simple arithmetic average of the observed values. The reported primary treatment contrast is the difference between the adolescent erenumab and placebo LSMs. The registry gives standard errors for the arm estimates and a sponsor-reported confidence interval for the contrast.

How should the re-calculation be distinguished from the trial analysis?

The unadjusted re-calculation uses posted arm-level summaries to form a simple comparison. It does not have the participant-level repeated measurements or the model adjustment described in the registry. The reported sponsor estimate is therefore the more relevant result for the trial’s prespecified primary analysis. The close numerical agreement between the sponsor result and the recalculation is reassuring as a consistency check, but it does not make the methods interchangeable.

The reported p-value assesses how compatible the data are with a null hypothesis of no difference under the assumptions of the stated analysis. A p-value is not a measure of effect size, and it does not tell readers the probability that a treatment effect is true. The confidence interval provides a range of estimates compatible with the data and model at the stated confidence level; its width conveys uncertainty. Neither statistic alone resolves issues such as clinical importance, missing data, or generalizability.

What does over-dispersion mean in general?

Over-dispersion is a general concern for count outcomes when their variability is greater than a simple model assumes. If the model understates variability, standard errors can be too small and confidence intervals too narrow. Monthly migraine days are counts, but the registry describes a linear mixed effects repeated measures model for the primary analysis. It does not report a separate over-dispersion assessment, so no conclusion about whether over-dispersion was evaluated can be drawn from the registry record.

The endpoint is a change score interpreted through a model that includes baseline and repeated visits. The registry does not give details of distributional checks, covariance structure, estimation procedure, or sensitivity analyses. Such information can matter when assessing whether model assumptions are adequate, but it is not reported in the registry record.

Only adolescent results are presented for the primary analysis, as specified in the statistical analysis plan according to the registry description. The full analysis set is defined as randomized adolescent participants with Month 3 data available. The record does not describe how missing measurements were handled, whether participants with incomplete repeated measurements contributed to model estimation, or whether additional analyses tested the effect of missing data assumptions. Those omissions limit independent assessment of the analysis population and robustness, without changing the reported result.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate is a difference in least squares mean change of -0.08 days per month, with a 95% confidence interval from -1.80 to 1.65. The interval spans zero and includes estimates favoring either group under the contrast convention, so the point estimate alone should not be treated as a precise measure of the direction or size of a group difference.

In general, a confidence interval summarizes uncertainty around an estimate under the statistical model and its assumptions. A narrower interval indicates greater precision than a wider interval on the same scale. The primary interval remains compatible with a range of between-group differences, including no difference. It does not prove that the groups are equivalent; an equivalence conclusion would require a prespecified equivalence margin and an analysis designed for that purpose, neither of which is reported in the registry record.

The simple unadjusted re-calculation gives a 95% confidence interval from -1.812 to 1.652. Its endpoints are close to the sponsor-reported interval, while the sponsor result remains the inferential analysis to prioritize. The small difference in displayed endpoints is consistent with differing methods and rounding; the registry reports the sponsor interval to two decimal places and the recalculated interval to three.

The point estimate and interval describe statistical precision for the primary contrast, not the importance of any possible difference to participants. The registry record does not report a threshold for a clinically meaningful difference in monthly migraine days. Precision also applies specifically to adolescents in the stated Month 3 analysis, not automatically to children, other time points, or outcomes such as disability and headache severity.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for 80% power and participants per arm for 90% power. They are not total events. They are illustrations based on the observed effect for each comparison, not the trial’s original design calculation. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row considers the stated fraction of the observed effect: the full observed effect, 75% of the observed effect, or 50% of the observed effect.

In general, 80% power means that a study planned under the stated assumptions would have an 80% chance of detecting an effect of the specified size at the chosen significance level, if that effect were the true effect and the assumptions held. The 90% column represents a higher planned chance of detecting that specified effect, and therefore generally calls for a larger sample. These are planning illustrations, not observed power.

The observed primary contrast is very small, so planning calculations that use it as the effect to detect produce very large participant counts. Smaller target effects require more participants because they are harder to distinguish from random variation. The same principle applies when planning for a fraction of the observed effect: targeting a smaller effect yields a larger required count. These calculations should not be read as a judgment about the trial’s design quality or as evidence that the trial was intended to detect the observed effect. The original sample-size justification and assumptions are not reported in the registry record.

Different outcomes can yield very different planning illustrations because their observed effects, scales, and variability differ. The calculations are based on simplified assumptions and should be used as a guide to how precision and target effect size affect planning, not as a replacement for a design-specific sample-size analysis.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.080; pooled standard deviation σ = 6.875.
2. n = 2 × (1.96 + 0.842)² × 6.875² / -0.080² = 115,918.9, rounded up to 115,919 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.0800000000000001                      # observed difference in means
sigma <- 6.87461217087917                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3832998)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 115,919 (80% power), 155,183 (90% power)
 75% of observed effect: n per arm = 206,078 (80% power), 275,880 (90% power)
 50% of observed effect: n per arm = 463,676 (80% power), 620,730 (90% power)
power.t.test: 115919.8 
Simulated power at n = 115,919 per arm: 0.796 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis is a difference in least squares means of -0.08, with a 95% confidence interval from -1.80 to 1.65 and p = 0.93. This is the result from the stated linear mixed effects repeated measures analysis, which includes baseline and other listed model terms.

The unadjusted re-calculation based on posted summary statistics gives a difference of -0.08, a 95% confidence interval from -1.812 to 1.652, and p = 0.928. The estimates are numerically close. Small discrepancies in interval endpoints and p-values can arise because the re-calculation uses summary statistics and a simpler comparison, while the sponsor’s result comes from the trial’s model and is displayed with different rounding.

The sponsor’s own analysis takes precedence for interpretation of the prespecified primary comparison. The recalculation is a check based on the posted arm summaries, not a replacement for the model-based analysis. The registry record does not indicate a discrepancy requiring a different interpretation.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several statistical hypotheses are evaluated. Even if each test is conducted at a conventional significance level, the chance of at least one false-positive finding across a collection of tests can increase. Researchers may address this with a prespecified testing sequence or adjustment, but the registry record does not report a multiplicity procedure for the secondary outcomes. The primary result is identified as the primary endpoint, while the secondary outcomes should be interpreted with caution when considering multiple comparisons.

The registry describes the primary model and says that adolescent results alone are presented as prespecified in the statistical analysis plan. It does not report the complete statistical analysis plan, a hierarchy for secondary hypotheses, or whether any multiplicity adjustment was applied. Therefore, the status of secondary results as confirmatory or exploratory cannot be fully reconstructed from the registry record.

Missing outcome data are another important consideration. The primary full analysis set is described as randomized adolescents with data available during Month 3. The record does not report the amount or pattern of missing primary outcome data, the method used to handle missing observations, or sensitivity analyses under alternative missing-data assumptions. A repeated-measures model can use available measurements under its modeling assumptions, but the registry description does not establish which missing-data assumptions were used or whether they were tested.

The analysis population is also specific: the primary result is for adolescents, despite enrollment of children and adolescents. This is stated to follow the statistical analysis plan. The results for children are not included in the primary efficacy presentation, and a separate primary estimate for that age group is not reported in the registry record. This limits what can be concluded about the trial’s full pediatric population from the primary result.

The registry record does not report interim efficacy analyses or the original sample-size justification. Those details cannot be inferred from the completed status, enrollment, or the posted endpoint estimates. Their absence does not invalidate the reported analysis, but it limits independent assessment of planning, monitoring, and the complete inferential framework.

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: sinusitis bacterial (8.3%), obesity (8.3%), asthma (8.3%), upper respiratory tract infection (7.1%), migraine (7.1%).

The registry lists serious adverse events for separate treatment groups and phases. During the double-blind treatment phase, serious adverse events were reported for 6 of 129 adolescent participants in the placebo group and 4 of 132 adolescent participants in the erenumab group. Among children in that phase, the corresponding counts were 1 of 14 with placebo and 0 of 9 with erenumab. The listed deaths were 0 in each group.

These are counts of participants with serious adverse events among the stated at-risk groups. They are not the primary efficacy analysis denominators: the primary endpoint used 118 placebo and 124 erenumab adolescent participants with Month 3 data. The difference in denominators reflects the distinct registry listings and populations and should be kept in mind when comparing efficacy and safety information.

The record also includes separate dose-level groups for a later phase, with their own at-risk totals and serious-event counts. Those groups should not be merged with the double-blind treatment-phase counts without details about exposure and analysis rules. Serious-event counts alone do not describe all adverse events, their timing, severity, or causal relationship to treatment. The registry record lists other adverse-event counts separately, but the serious-event figures by themselves are not a complete safety assessment.

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

The primary result estimates the difference between erenumab and placebo in model-adjusted change in monthly migraine days at Month 3 among adolescent participants with available Month 3 data. The sponsor-reported point estimate is close to zero, and its confidence interval includes zero while covering differences in either direction. This is an uncertain estimate of the contrast for that specific outcome, population, and time point.

The result does not establish that the groups are equivalent. A failure to show a clear difference is not the same as proving there is no difference. The registry record does not report an equivalence margin or a noninferiority framework for the primary question. The p-value should not be interpreted as the probability that erenumab has no effect or that the observed estimate is due to chance.

The result also does not answer every question raised by the trial. It does not provide the primary efficacy result for children, establish what happened beyond Month 3, or determine outcomes not reported in the registry record. The secondary outcomes offer related information but have their own uncertainty and multiplicity considerations. The serious adverse-event counts are descriptive and do not, on their own, establish comparative safety.

Finally, the registry reports the result for a defined analysis population, not every enrolled participant. The overall enrollment was 284, while the primary analysis is restricted to randomized adolescents with Month 3 data. The registry does not report enough missing-data detail to assess fully how unavailable measurements may affect the estimate. Interpretation should remain tied to the population, endpoint, analysis, and follow-up period explicitly reported.

18. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the distinction between an estimated effect and the uncertainty around that estimate. The primary point estimate is small, but the confidence interval is wide enough to include values on both sides of zero. A single point estimate therefore cannot convey the range of contrasts compatible with the analysis.

The analysis also demonstrates why a model-based estimate should be distinguished from a simple summary-statistic comparison. The trial’s repeated-measures model adjusts for baseline and specified factors and accounts for participants as a random effect. An unadjusted recalculation provides a useful consistency check, but it does not reproduce those design and modeling features.

Population definition matters as much as the statistical method. The trial enrolled both children and adolescents, yet the reported primary efficacy result is adolescent-only. Readers who treat the primary estimate as applying to all pediatric participants would extend the evidence beyond the analysis reported in the registry.

Finally, the registry record makes clear that planning illustrations based on an observed effect are not descriptions of the trial’s original design or observed power. The sample-size rationale, missing-data strategy, and multiplicity approach are not fully reported. These distinctions help separate what the posted estimate supports from questions that remain unresolved by the registry 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 most important trial-specific limitation for interpreting efficacy is that the primary results are presented only for adolescents, even though the study included children. The primary result therefore cannot be used as a direct estimate for the child group. A separate primary efficacy estimate for children is not reported in the registry record.

The primary endpoint is limited to change in monthly migraine days at Month 3. It does not establish the pattern at other periods or longer-term outcomes. The registry’s reported primary analysis population includes randomized adolescents with Month 3 data, but the amount and pattern of missing data and the approach to missing measurements are not reported. This leaves uncertainty about how incomplete outcome data may affect the estimate.

The model description gives its main terms but not details such as covariance structure, distributional diagnostics, or sensitivity analyses. The registry record also does not report the original sample-size justification or interim analysis plans. Although five secondary outcomes are identified, numerical results are not reported for every listed secondary outcome, and a multiplicity procedure is not described. These gaps limit assessment of the complete analysis strategy and the consistency of findings across outcomes.

Safety counts are reported for different groups and phases, with at-risk totals that differ from the efficacy denominators. The counts are descriptive and do not include enough detail by themselves to characterize event timing, exposure, or causality. These limitations call for a narrow reading of each estimate rather than a broad conclusion across all ages, outcomes, and phases.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Erenumab in Pediatric Subjects With Chronic Migraine — NCT03832998.
• Registry record last updated 2026-10-28; status last verified 2026-10.
• Results first posted 2026-10-28.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed Phase 3 randomized, quadruple-masked, parallel-group, placebo-controlled trial of erenumab in children and adolescents with chronic migraine. Overall enrollment was 284. The primary endpoint was change from baseline in monthly migraine days at Month 3, and the posted primary efficacy analysis was restricted to adolescents with Month 3 data.

The sponsor-reported difference in least squares mean change was -0.08 days per month, with a 95% confidence interval from -1.80 to 1.65 and p = 0.93. This estimate is compatible with a range of between-group differences and does not establish equivalence. The registry also lists secondary efficacy and safety outcomes, but some analysis details and results are not reported in the registry record.