Eptinezumab in Participants With Episodic Cluster Headache: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Eptinezumab in Participants With Episodic Cluster Headache (NCT04688775), a randomized phase 3 study. The primary outcome is Change From Baseline in the Number of Weekly Cluster Headache (CH) Attacks, Averaged Over Weeks 1-2.

2. Clinical Question

3. Trial Design

The registry describes a phase 3, randomized, double-blind, parallel-group, placebo-controlled delayed-start study. It was sponsored by H. Lundbeck A/S and is marked completed. The registry lists a start date of 2020-12-23 and a primary completion date of 2023-06-14. Enrollment is listed as 231 participants. Those record details describe the planned and recorded framework, but do not by themselves establish how complete the outcome data were or how closely the study conduct matched the plan.

The two sequences were eptinezumab followed by placebo, and placebo followed by eptinezumab. The first period was placebo-controlled; the later period involved delayed start of eptinezumab for the group initially assigned placebo. Consequently, the cleanest randomized contrast is the placebo-controlled period, before both sequences have received active treatment. Results from a later period may answer different questions and should not automatically be treated as another placebo-controlled comparison.

Random allocation and double masking are design features intended to reduce systematic differences between groups and influence from knowledge of assignment. The parallel-group label describes comparison of groups rather than a crossover in which each participant is compared against themself. Although the treatment sequences include a transition, the registry identifies the study model as parallel-group.

The registry record does not report the original sample-size justification, the planned statistical analysis in full, interim analyses, or details of randomization and masking procedures in the information summarized for this analysis. It also does not report the eptinezumab dose or the exact infusion schedule in that information. Those omissions limit what can be concluded about the original design assumptions and implementation from this record alone.

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.

Placebo-controlled Period

Reasons for not completing this period:

Delayed Start Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The APRS included all randomized participants.

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 all-participants-randomized-set (APRS) included all randomized participants. The all-participants-treated set (APTS) included all randomized participants who received infusion with double-blind investigational medicinal product (IMP). Demographic characteristics were collected for the APTS and study-specific characteristics were collected for the APRS.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in the Number of Weekly Cluster Headache (CH) Attacks, Averaged Over Weeks 1-2, measured over Baseline (Week 0), Weeks 1-2.

The primary endpoint is change from baseline in the number of weekly cluster headache attacks, averaged over Weeks 1-2. Baseline is identified as Week 0. Participants recorded attack information in a daily electronic diary, including whether attacks occurred and the start date and time of each attack. The diary also captured headache characteristics and use of acute medication. The primary measure therefore reflects a count-based symptom frequency summarized over a short post-baseline interval.

A change-from-baseline endpoint expresses the outcome relative to each participant’s starting measurement, rather than only comparing follow-up values. The reported group values are least-squares means, which are model-based adjusted averages; their exact adjustment details are not reported in the registry record. A negative group change indicates fewer weekly attacks relative to baseline. The between-group estimate is the relevant quantity for the comparative question, because both groups may change over time, including through natural variation or other influences.

Weekly attack frequency is used because it directly represents the clinical feature named in the study question, and averaging over Weeks 1-2 gives a defined early assessment period. A mean can summarize the group’s pattern, but does not describe every participant’s experience or the spread of individual responses. The registry record does not report a threshold for an individually important change or a minimum clinically important difference. Statistical evidence about the group comparison therefore should not be equated with a determination of clinical importance.

7. Results Posted in the Registry

• Eptinezumab: mean -4.00 versus -4.60 on control; difference 0.60 (95% CI -1.92 to 3.12), standardized effect d = 0.06; z-test p = 0.641.

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.

Number of Participants With ≥50% Reduction From Baseline in Number of Weekly Attacks Over Weeks 1-2

• 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:
  • Eptinezumab: 38.9% (44/113) versus 31.4% (37/118) on control; risk difference 7.6 percentage points (95% CI -4.7 to 19.9), risk ratio 1.24 (0.87–1.77); unadjusted two-proportion z-test p = 0.227.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Eptinezumab and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in the Number of Weekly Times an Abortive Medication Was Used, Averaged Over Weeks 1-2

• 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:
  • Eptinezumab: mean -2.54 versus -3.55 on control; difference 1.01 (95% CI -1.64 to 3.66), standardized effect d = 0.10; z-test p = 0.455.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Eptinezumab and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in the Number of Daily Attacks, Averaged Over Days 1-3

• 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:
  • Eptinezumab: mean -0.22 versus -0.35 on control; difference 0.13 (95% CI -0.30 to 0.56), standardized effect d = 0.08; z-test p = 0.553.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Eptinezumab and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary outcomes spanning attack reduction, acute medication use, daily attack frequency, pain ratings, and time to resolution. Across the outcomes with detailed summaries in the record, the point estimates do not establish a consistent comparative advantage for eptinezumab. Their uncertainty intervals include no difference, and the unadjusted comparisons are not statistically clear. This general pattern is compatible with the uncertain primary comparison rather than serving as an independent confirmation of a distinct effect.

Secondary outcomes can add useful context because they describe different dimensions of the condition and can indicate whether the primary result aligns with other measures. However, measures may differ in scale, timing, and interpretation. A result on attack frequency, medication use, or pain intensity is not interchangeable with the primary weekly attack measure. Nor should a numerical change in one outcome be taken as proof of a corresponding change in another.

The registry reports 29 outcome measures and 28 posted secondary outcomes. Looking across many outcomes creates a multiplicity concern: even if there is no underlying treatment difference, some comparisons can appear more striking by chance. The registry record does not report a multiplicity adjustment or a prespecified testing hierarchy for secondary outcomes. Accordingly, unadjusted secondary p-values and intervals carry less weight than the primary analysis and should be treated as exploratory unless further analysis plans establish otherwise.

The full set of secondary summaries should be considered alongside the primary endpoint, the methods used, and the uncertainty around each estimate. No single secondary result can resolve the primary uncertainty, and a collection of unadjusted comparisons does not become confirmatory simply because several outcomes were recorded.

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

• Number of Participants With ≥50% Reduction From Baseline in Number of Weekly Attacks Over Weeks 1-2
• Change From Baseline in the Number of Weekly Times an Abortive Medication Was Used, Averaged Over Weeks 1-2
• Change From Baseline in the Number of Daily Attacks, Averaged Over Days 1-3
• Change From Baseline in the Number of Days With <3 Attacks Per Day, Averaged Over Weeks 1-2
• Time From First Infusion of IMP to Resolution of Cluster Headache Bout Within the First 4 Weeks
• Change From Baseline in Number of Attacks Starting ≤24 Hours After the Start of the First Infusion of IMP
• Change From Baseline in the Daily Mean Score on 5-Point Self-Rating Pain Severity Scale, Averaged Over Days 1-3
• Change From Baseline to Week 1 in the Number of Weekly Attacks

9. Statistical Interpretation

10. Statistical Methods Explained

The registry’s primary outcome is continuous: it is a numerical change in weekly attack frequency. The reported group summaries are least-squares means, accompanied by standard errors. A standard error describes the statistical uncertainty in an estimated group mean; it is not a measure of the spread of individual participants’ outcomes. Smaller standard errors generally indicate more precise estimates, but interpretation of a comparison also depends on the uncertainty in the difference between groups.

What does the sponsor’s repeated-measures method do?

The reported method is Mixed Models Repeated Measures. In general, a repeated-measures model analyzes observations collected at multiple time points while accounting for the fact that measurements from the same participant tend to be related. It can use the pattern of available measurements across time to estimate group differences, subject to the model’s assumptions and specified handling of missing observations. The registry record does not provide the full model specification, covariance structure, covariates, or missing-data assumptions, so those details cannot be evaluated from the recorded result alone.

The sponsor reports a mean difference in final values of 0.7, with a 95% confidence interval from -1.3 to 2.6 and p = 0.505. The registry labels the analysis as a superiority analysis. The result is a model-based comparison, not a direct statement about each participant’s response. Its interval includes zero, so it does not show a statistically clear difference at conventional levels. The registry record does not report a non-inferiority or equivalence margin; a superiority result that is not statistically significant cannot be reinterpreted as evidence of equivalence.

What is the recalculation?

The unadjusted recalculation uses the posted group summaries to estimate a simple difference between the eptinezumab and placebo means. It yields 0.6, with a 95% confidence interval from -1.923 to 3.123 and p = 0.641. The calculation is explicitly approximate because the standard deviations used for the comparison are inferred from the posted standard errors. It does not reproduce the sponsor’s repeated-measures model, its adjustments, or its use of repeated observations. It is useful as a transparent check on the direction and rough scale of the posted summaries, not as a substitute for the sponsor’s analysis.

The recalculated confidence interval is a range of values compatible with the data under the calculation’s assumptions. Because it includes zero, the results do not distinguish a positive difference from a negative one with the stated level of precision. The p-value describes how unusual data at least as inconsistent with a zero-difference model would be under that model and its assumptions. It is not the probability that the null hypothesis is true, nor a measure of the probability that treatment benefits an individual.

Why can count outcomes be challenging?

Attack counts are nonnegative counts and may not behave like normally distributed continuous measurements. Counts can be skewed, include many low values, or vary more than a simple count model expects. In general, over-dispersion means that observed variability exceeds the variability assumed by a basic count model; ignoring it can make uncertainty estimates too optimistic. The registry’s primary result is reported as a least-squares mean comparison, but the record does not report enough model details to determine the exact distributional assumptions or whether over-dispersion adjustments were used.

The posted primary description says participants recorded attacks in a daily diary and the outcome was averaged over Weeks 1-2. The diary-based measure is a useful way to define repeated symptom counts, but it depends on recording behavior and complete, accurate entries. The registry record does not report diary completion rates, rules for incomplete diaries, or how missing days were handled.

How should the secondary analyses be viewed?

The binary secondary outcome reports the number of participants meeting a threshold of at least 50% reduction in weekly attacks. A risk difference expresses the difference between the groups’ event proportions; its confidence interval describes uncertainty in that difference. The posted interval crosses zero, so the data do not establish a clear group separation for that outcome. The other secondary summaries are changes in continuous measures. Their recalculated comparisons are unadjusted and should be read as descriptive checks rather than as replacements for a prespecified model.

Many outcomes were listed, including attack frequency, acute medication use, pain severity, and time to resolution. Testing or examining many outcomes increases the chance that some may appear notable by chance. The registry record does not report a multiplicity adjustment or a hierarchy specifying which secondary analyses would be confirmatory. In general, results from unadjusted secondary comparisons therefore carry less evidential weight than a well-specified primary analysis.

The sample-size illustrations use observed effects and stated planning assumptions. They are not the trial’s original design calculations, and they do not establish what the study was capable of detecting under its actual design. The registry record does not report the original sample-size justification or the trial’s planned power calculation.

11. Confidence Intervals and Precision

The primary recalculated difference is 0.6 weekly attacks, with a 95% confidence interval from -1.923 to 3.123. The interval describes the uncertainty around the estimated between-group difference under the assumptions of this unadjusted calculation. It includes zero, as well as values on either side of zero. The data therefore do not pin down the direction of the difference with precision sufficient to exclude no difference.

The sponsor-reported model-based estimate is 0.7, with a 95% confidence interval from -1.3 to 2.6. This interval also includes zero. It is narrower in numerical span than the recalculated interval, but the estimates come from different methods, so their width should not be treated as a direct contest between analyses. The sponsor result reflects the reported repeated-measures model; the recalculation is a simple approximation from group summaries.

A confidence interval is not a guarantee that the true effect lies within its endpoints, nor does an interval containing zero prove that the true effect is zero. Rather, it indicates the range of effects compatible with the observed data under the procedure’s assumptions. The registry record does not give a clinically important difference threshold, so the endpoints cannot be classified as clinically trivial or important from this information alone.

Standard errors reported beside the group least-squares means describe uncertainty in those means, not participant-to-participant variability. A narrow estimate for each group does not necessarily imply a narrow interval for the difference. Precision of a comparison depends on both group estimates and their relationship in the analysis, among other factors. The full covariance and model details are not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are hypothetical design calculations based on the observed effect, not a reconstruction of the trial’s original design. For these continuous and binary outcomes, the listed values are participants per arm. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the target effect is the stated fraction of the observed effect. The registry record does not report the original sample-size assumptions or justification.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect if that effect were the true one and the planning assumptions held. The 90% power column gives the corresponding per-arm figure for a higher chance of detection under those same assumptions. These are planning probabilities, not probabilities that the result is true, and not a measure of the probability that this completed trial detected an effect. This is not observed power.

Each row changes the assumed effect to detect: the full observed effect, 75% of the observed effect, or 50% of the observed effect. A smaller target effect is harder to distinguish from random variation, so the required number of participants per arm grows. For the primary outcome, the displayed illustration is based on the recalculated observed mean difference. That estimate is uncertain, as reflected by its confidence interval; a planning calculation based on it inherits that limitation and should not be treated as a reliable prediction of a future study’s requirements.

The registry’s general planning note says time-to-event illustrations, where applicable, give total events rather than participants per arm. That distinction does not change the reading of the participant-per-arm figures for the outcomes. The illustrations are not observed trial results and do not imply that the original study was designed using those calculated values.

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 = 0.600; pooled standard deviation σ = 9.775.
2. n = 2 × (1.96 + 0.842)² × 9.775² / 0.600² = 4,166.6, rounded up to 4,167 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 <- 0.6                      # observed difference in means
sigma <- 9.7751817906012                     # 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(4688775)
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 = 4,167 (80% power), 5,578 (90% power)
 75% of observed effect: n per arm = 7,408 (80% power), 9,917 (90% power)
 50% of observed effect: n per arm = 16,667 (80% power), 22,312 (90% power)
power.t.test: 4167.6 
Simulated power at n = 4,167 per arm: 0.800 (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 Mixed Models Repeated Measures comparison. It gives a mean difference of 0.7, a 95% confidence interval from -1.3 to 2.6, and p = 0.505. This is the trial’s reported model-based result and should take precedence over a simple recalculation when describing the sponsor’s analysis.

The recalculated result is an unadjusted comparison from posted summary statistics: a difference of 0.6, with a 95% confidence interval from -1.923 to 3.123 and p = 0.641. The point estimates are close, and both intervals include zero. However, the methods differ. The recalculation approximates variability from the posted standard errors and does not reproduce the sponsor’s repeated-measures model or its specific assumptions.

The registry record marks no discrepancy between the sponsor result and the recalculation. That does not make the recalculation a second independent analysis, nor does it increase the amount of evidence. It is best read as a limited consistency check on the general direction and scale of the reported comparison. The sponsor’s analysis remains the appropriate reference for the trial’s stated inferential result, while the recalculation helps illustrate how the posted summary statistics compare under a simpler approach.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 29 outcome measures, including 28 secondary outcomes. Evaluating multiple endpoints creates an opportunity for chance findings. Statistical methods can address this concern by adjusting significance thresholds, controlling a family-wise error rate, controlling a false-discovery rate, or establishing a prespecified hierarchy in which outcomes are tested in a defined order. The registry record does not report whether any such strategy was planned or used. Without that information, the secondary comparisons should be regarded as unadjusted unless stated otherwise, and their evidential weight is limited.

The record identifies the primary population as the APRS, including all randomized participants. That provides an important population description, but the registry information does not report the detailed analysis-population rules, exclusions, or how participants with incomplete outcome data contributed to the model. The primary endpoint is diary-based. The record does not report diary completion, missing-data rates, imputation procedures, sensitivity analyses, or the assumptions used for missing observations. These details matter because missing outcomes can affect both the estimated group means and the uncertainty around the comparison.

Repeated-measures models can, in general, use available observations without requiring every participant to have a complete series, but their validity depends on model specification and assumptions about missingness. The record does not provide enough information to judge those assumptions or establish whether alternative analyses were conducted. No conclusion about the impact of missing data should be inferred from the reported estimates alone.

The registry record also does not report interim analyses, stopping rules, or the full prespecified statistical analysis plan. Their absence from this information does not establish that such procedures were absent from the study; it means they are not reported in the registry record. These gaps limit assessment of selective testing, deviations from the planned analysis, and the robustness of the reported result.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anaphylactic reaction (0.9%), meningitis enteroviral (0.9%), bladder cancer (0.9%), hypersensitivity (0.9%), urinary incontinence (0.9%).

The registry reports serious adverse event counts for each treatment sequence and period, alongside the number at risk for those summaries. In the placebo-controlled period, the eptinezumab group had 2 serious adverse events among 112 at risk, and the placebo group had 0 among 117 at risk. In the delayed-start period, the eptinezumab-to-placebo sequence had 2 among 108 at risk, while the placebo-to-eptinezumab sequence had 1 among 107 at risk. Deaths are reported as 0 in each of the four period groups.

These are descriptive counts, not a formal estimate of comparative risk. The periods and sequences should be kept distinct, particularly because treatment exposure changes in the delayed-start period. A count of zero in a group does not establish that an event is impossible, and small event counts provide limited precision about uncommon harms. The registry lists several serious-event terms at 0.9% each: anaphylactic reaction, meningitis enteroviral, bladder cancer, hypersensitivity, urinary incontinence, and cystocele. The record does not provide enough information in this summary to attribute each event causally to treatment or to assess its clinical context. Safety findings should be interpreted as recorded events, not proof of causation.

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

The primary result answers a specific question: how the average change in weekly cluster headache attacks over Weeks 1-2 compared between the randomized groups. The posted group means both show reductions from baseline. The between-group estimates, however, have confidence intervals that include zero, and the reported p-values do not indicate a statistically clear difference. The data therefore do not establish a difference between eptinezumab and placebo on this primary endpoint.

That conclusion is not the same as proving that the treatments are identical, or that eptinezumab has no effect. The confidence intervals remain compatible with differences in either direction, and the record does not identify a threshold for clinical importance. A statistically non-significant result can reflect a small effect, imprecision, or both; the available results do not separate those possibilities conclusively.

The endpoint covers a defined early period and a specific symptom measure. It does not, by itself, establish effects on other outcomes, longer-term disease course, or the experience of every participant. Group averages conceal variation in individual responses. Secondary outcomes provide additional dimensions but are numerous and not reported with a multiplicity strategy, so they cannot be treated as a set of independent confirmatory tests.

The safety counts describe serious adverse events recorded in the reported periods. They do not establish causation, rule out uncommon events, or provide a complete assessment of all possible harms. The registry record and posted results should therefore be read as evidence about the measured outcomes under this study’s recorded design, not as a complete account of benefit and risk in every setting.

In short, the record documents a randomized comparison and a sponsor-reported model-based analysis, but the primary comparative result remains uncertain. It supports neither a definitive claim of superiority nor a claim of equivalence. Broader conclusions would require considering the full study report, analysis details, and other relevant evidence, none of which should be assumed from the registry entry alone.

18. Why This Trial Matters Statistically

This trial illustrates why the direction of within-group change is not the same as evidence of a between-group effect. Both groups had negative mean changes in weekly attacks, but the scientific question is whether their changes differ. A control group helps account for changes that may occur over time independent of the active treatment, such as natural fluctuation, diary effects, or other influences. Interpreting each group’s change alone would not answer the randomized comparison.

It also demonstrates the importance of distinguishing a model-based reported analysis from an unadjusted recalculation. The sponsor’s repeated-measures analysis and the simple summary-statistic calculation produce similar point estimates, but they rely on different methods and assumptions. Keeping those roles clear avoids treating a convenient calculation as if it were the trial’s prespecified analysis.

Precision is central to interpretation. The primary confidence intervals cross zero, so they do not rule out no difference or differences in either direction. The absence of a statistically clear result should not be converted into a claim of equivalence. Conversely, observed reductions within both groups do not establish a treatment-specific benefit.

The broad set of secondary outcomes adds a further statistical lesson: multiple measures can be informative, but without a reported testing strategy, isolated unadjusted findings deserve caution. Finally, planning illustrations derived from an observed effect are not evidence about the trial’s original design or its observed power. Together, these features show why a registry result needs to be read through its estimand, model, uncertainty, outcome multiplicity, and reporting limits.

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 primary outcome is based on participant diary records. The registry describes daily recording but does not report diary completion, validation, or rules for handling incomplete entries. Missing or inconsistently recorded attack data could influence estimated changes, and the record does not provide enough detail to assess that possibility.

The endpoint averages attack counts over Weeks 1-2, so the result addresses an early period rather than a long-term outcome. The registry record does not report a clinically important difference threshold, making it difficult to determine whether values within the confidence interval would be important to participants. The least-squares means are model-based, but the full model specification and adjustment variables are not reported in the information summarized for this analysis.

The delayed-start structure requires attention to period and treatment sequence. The placebo-controlled period supports the initial randomized contrast; later results arise after the initially placebo-treated sequence begins eptinezumab. Those periods should not be combined or interpreted as if they provide the same randomized placebo comparison. The summary information does not provide sufficient detail to assess period-specific modeling or possible carryover considerations.

The sponsor’s analysis is reported, but the registry record does not provide the full statistical analysis plan, missing-data sensitivity analyses, or multiplicity procedures. The unadjusted recalculation is only an approximation from summary statistics and cannot reproduce the repeated-measures model. Secondary findings are subject to multiplicity concerns, while safety counts are too descriptive to establish causation or precisely characterize rare risks. These limitations qualify interpretation of the posted estimates without changing the values recorded.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Eptinezumab in Participants With Episodic Cluster Headache — NCT04688775.
• Registry record last updated 2024-08-09; status last verified 2024-07.
• Results first posted 2024-08-09.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed phase 3 randomized, double-blind, parallel-group, placebo-controlled delayed-start study of eptinezumab in participants with episodic cluster headache. Enrollment is listed as 231. The primary endpoint was change from baseline in weekly cluster headache attacks averaged over Weeks 1-2.

The sponsor-reported repeated-measures analysis estimated a mean difference of 0.7, with a 95% confidence interval from -1.3 to 2.6 and p = 0.505. The unadjusted recalculation is 0.6, with a 95% confidence interval from -1.923 to 3.123 and p = 0.641. Both intervals include zero, leaving the comparative primary result uncertain. The registry record does not report the full statistical plan, multiplicity strategy, or detailed missing-data methods.