A Study of Galcanezumab in Participants With Chronic Cluster Headache: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Galcanezumab in Participants With Chronic Cluster Headache (NCT02438826), a randomized phase 3 study. The primary outcome is Overall Mean Change From Baseline in Weekly Cluster Headache Attack Frequency.

2. Clinical Question

This is a comparison of average change over the treatment period, not a direct comparison of whether every participant improved. The primary result is an adjusted comparison of group means, and the registry also reports several secondary measures, including response thresholds and patient-reported improvement. Those outcomes can provide additional context, but they do not replace the primary question.

3. Trial Design

The registry describes a Phase 3, randomized, double-blind, parallel-group, placebo-controlled study of galcanezumab for chronic cluster headache. The listed enrollment is 240. During the double-blind treatment phase, participants received either galcanezumab 300 mg or placebo once a month by subcutaneous injection for 3 months. The study then included a long-term open-label extension, with galcanezumab 300 mg administered every 30 days for up to a total of 12 administrations.

Randomization is intended to create groups that can be compared while reducing the influence of systematic allocation choices. Double blinding means treatment assignment was masked during the blinded phase, which can limit some differences in care or outcome reporting associated with knowing the assignment. The parallel design means the study compares groups assigned to different treatments rather than comparing each participant with themself across treatment sequences.

The primary outcome record lists 120 participants in the placebo group and 117 in the galcanezumab group. Its analysis population is described as randomized participants who received at least 1 dose and had baseline and at least one post-baseline value. This is the population specified for the posted primary outcome, and should not be assumed to describe every outcome or every phase of follow-up.

The registry record lists the study as completed. It does not report the original sample-size justification, the assumptions used to plan the trial, or whether interim analyses were conducted. The planning illustrations associated with the posted results are separate from those original design decisions.

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: Study consists of a 12-week double-blind treatment phase; an optional 1-year open-label treatment phase; and a 16-week post-treatment phase (washout).

Double-Blind Treatment Phase

Reasons for not completing this period:

Open-Label Treatment Phase

Reasons for not completing this period:

Post-Treatment Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants who received at least 1 dose of study drug, and had baseline and at least one post baseline value.

5. Baseline Characteristics

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

Population: All randomized participants who received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Overall Mean Change From Baseline in Weekly Cluster Headache Attack Frequency, measured over Baseline, Week 1 through Week 12.

The primary endpoint is the overall mean change from baseline in weekly cluster headache attack frequency, reported in cluster headache attacks per week. Participants recorded attacks daily in an electronic diary. The diary data for baseline and the double-blind treatment phase were organized into 14-calendar-day intervals: baseline and successive pairs of study weeks through Week 12. The interval results were adjusted to a 7-day frequency so that the outcome could be expressed as attacks per week.

A change-from-baseline endpoint describes how the measured value during follow-up differs from the starting value. The overall mean summarizes the group’s average change across the specified assessment period. In this study, the primary result is an adjusted least-squares mean estimate from a mixed model repeated measures analysis, rather than a simple unadjusted average of all diary values.

Weekly attack frequency is used because it expresses the symptom measure in a consistent time unit while drawing on repeated diary observations. Repeated assessments can represent change over the treatment period more fully than a single observation. However, an average change does not describe the full range of individual experiences, and the group mean alone does not establish how many participants had a particular degree of improvement.

7. Results Posted in the Registry

• Galcanezumab 300 mg: mean -5.38 versus -4.59 on control; difference -0.79 (95% CI -3.01 to 1.43), standardized effect d = -0.09; z-test p = 0.485.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants With a 50% or Greater Reduction From Baseline in the Weekly Number of Cluster Headache Attacks

• 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:
  • Galcanezumab 300 mg: mean 32.60 versus 27.10 on control; difference 5.50 (95% CI -4.63 to 15.63), standardized effect d = 0.14; z-test p = 0.287.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Galcanezumab 300 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With a Sustained Response of 50% or Greater Reduction From Baseline in the Weekly Number of Cluster Headache Attacks

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Galcanezumab 300 mg: 16.2% (19/117) versus 17.5% (21/120) on control; risk difference -1.3 percentage points (95% CI -10.8 to 8.3), risk ratio 0.93 (0.53–1.63); unadjusted two-proportion z-test p = 0.796.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Galcanezumab 300 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With a 30% Reduction in the Weekly Number of Cluster Headache Attacks

• 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:
  • Galcanezumab 300 mg: mean 49.10 versus 39.00 on control; difference 10.10 (95% CI -0.99 to 21.19), standardized effect d = 0.23; z-test p = 0.074.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Galcanezumab 300 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts several secondary outcome measures, including attack-frequency response thresholds, sustained response, patient-reported improvement, and safety-related assessments. The posted response results do not form a single uniform pattern across definitions. Some measures are numerically more favorable in the galcanezumab group, while others do not show the same direction or degree of separation. This variation matters because the interpretation can depend on the outcome definition and observation period.

These endpoints complement the primary comparison by describing other aspects of response, but they do not overturn or replace the primary result. The primary endpoint is the registered main comparison of average change in weekly attack frequency. Secondary measures can help characterize the data, but a favorable result on one secondary measure would not by itself establish a consistent treatment effect across the study.

Many outcomes and analyses create opportunities for chance findings. Unless a testing strategy accounts for multiplicity, the probability of at least one apparently notable result across a collection of tests can be higher than for a single test. The registry record does not report whether or how multiplicity was controlled. The posted unadjusted secondary results therefore carry less weight than a prespecified primary analysis and should be interpreted cautiously, especially when considered separately.

The registry includes repeated entries for some named secondary outcomes and reports multiple outcome measures and analyses. It does not report enough detail to establish a complete hierarchy of hypotheses or which secondary comparisons were intended as confirmatory. Their role is best understood as additional descriptive evidence, not as a set of independent proofs.

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

• Percentage of Participants With a 50% or Greater Reduction From Baseline in the Weekly Number of Cluster Headache Attacks
• Percentage of Participants With a Sustained Response of 50% or Greater Reduction From Baseline in the Weekly Number of Cluster Headache Attacks
• Percentage of Participants With a 30% Reduction in the Weekly Number of Cluster Headache Attacks
• Percentage of Participants Reporting a Score of 1 or 2 on the Patient Global Impression of Improvement (PGI-I)
• Percentage of Participants Reporting a Score of 1 or 2 on the Patient Global Impression of Improvement (PGI-I)
• Percentage of Participants Reporting a Score of 1 or 2 on the Patient Global Impression of Improvement (PGI-I)
• Percentage of Participants With Suicidal Ideation Assessed by Columbia - Suicide Severity Rating Scale (C-SSRS)
• Percentage of Participants With Suicidal Behaviors Assessed by Columbia - Suicide Severity Rating Scale (C-SSRS)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint uses a mixed model repeated measures analysis. This general class of model analyzes repeated measurements from the same participant while accounting for their association over time. It can estimate average change at the study assessments while incorporating the pattern of repeated observations, rather than treating every diary assessment as unrelated. The registry describes least-squares means as the model-based estimates and lists treatment, sex, verapamil use, pooled investigative site, week, baseline, and treatment by week as fixed effects.

What is a least-squares mean?

A least-squares mean is a model-based group estimate adjusted for the variables included in the model. Here, the registry lists baseline and other fixed effects as part of the model. The estimate is therefore not necessarily identical to a raw arithmetic average. Such adjustment can make the comparison reflect the model’s specified structure, but its interpretation depends on the model and the analysis population actually used.

How should the treatment comparison be read?

The least-squares mean difference compares the adjusted mean change in the galcanezumab group with that in the placebo group. For change scores, negative values describe decreases from baseline. A difference of zero would mean equal adjusted mean change in the two groups. A difference below zero favors a larger decrease in the galcanezumab group on this outcome scale; a difference above zero favors a larger decrease in the placebo group. Direction alone is not enough to establish a clear difference: the confidence interval and the analysis must also be considered.

What does the confidence interval add?

A confidence interval describes uncertainty around an estimated effect. In general, a wider interval indicates less precision, while a narrower interval indicates more precision. For the registry’s primary result, the 95% confidence interval extends from -2.77 to 1.17. Because that range includes zero, the result is compatible with no between-group difference as well as with differences in either direction. A confidence interval is not a guarantee that the true value lies within its endpoints, and it does not measure the probability that a treatment works.

What is the role of the p-value?

A p-value evaluates how unusual the observed data, or data more extreme, would be under a specified null hypothesis and analysis model. It is not the probability that the null hypothesis is true, and it does not quantify the size or clinical importance of an effect. The registry’s primary p-value is 0.334. Read alongside the confidence interval and estimate, it does not provide strong evidence against the null hypothesis of no difference under the reported model.

Why distinguish the reported result from a re-calculation?

The simple re-calculation uses posted group summary statistics to estimate an unadjusted comparison. It does not reproduce the registry’s mixed model, which includes repeated measures and listed covariates. The recalculated mean difference is -0.79, with a 95% confidence interval from -3.008 to 1.428 and an unadjusted p-value of 0.485. These figures are a check based on summary data, not a replacement for the sponsor’s reported analysis. The registry record does not flag a discrepancy between the two results, but their methods differ, so they need not match exactly.

Why can repeated measures matter?

Diary measurements collected across time are correlated within a participant: observations from the same person are generally not independent in the way observations from different people may be. A repeated-measures model is designed to account for this structure. It can also model how treatment differences vary over assessment time through a treatment-by-week term. The registry does not report all model details, such as the covariance structure or the handling of incomplete repeated observations; those details are not reported in the registry record.

More broadly, statistical models depend on assumptions about the data and their structure. Model-based estimates can be sensitive to misspecification, missing observations, and influential measurements. The posted description identifies the model and fixed effects, but it does not provide enough information to assess every assumption or implementation detail. These limits do not invalidate the reported result; they define how much can be independently evaluated from the registry description.

11. Confidence Intervals and Precision

The reported primary estimate is -0.80 cluster headache attacks per week, with a 95% confidence interval from -2.77 to 1.17. The estimate is more precise than an unbounded statement that the groups differed, but the interval still covers a range that includes no difference and values in both directions. The span of the interval is important: the point estimate alone would conceal the uncertainty in the comparison.

In general, a confidence interval represents the range of effect values reasonably compatible with the observed data and the statistical model at the stated confidence level. It is not a range containing every participant’s outcome, and it is not a measure of individual response. The 95% label describes the long-run coverage property of the interval procedure under its assumptions; it does not mean there is a 95% probability that this specific interval contains the true effect.

The recalculated unadjusted interval, -3.008 to 1.428, is also consistent with a range of possible effects that crosses zero. It is based on posted summaries and does not reproduce the registry’s repeated-measures adjustment. The difference in interval endpoints between the two analyses reflects that they are not identical statistical procedures, not evidence that one can be selected solely because its result is more favorable.

Precision is influenced by the amount and variability of information, the analysis model, and the completeness of observations. The registry does not report enough detail to assess all of these factors. The appropriate interpretation is therefore tied to the posted model and its confidence interval, not to a claim that the treatment difference is exactly the point estimate or that effects outside the interval are impossible.

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 show participants per arm for the continuous and binary outcomes in the posted comparisons. They are not totals across arms and are not observed trial group sizes. The registry’s sample-size assumptions specify a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect were the true effect and the model assumptions held. The 90% power column expresses the corresponding planning target for a 90% chance. These are design calculations, not guarantees about a future study’s results.

Rows for planning at 100%, 75%, and 50% of the observed effect illustrate how the assumed target effect changes the required sample size. Smaller effects are harder to distinguish from random variation, so they require more participants under the same planning assumptions. The figures should be read as hypothetical planning illustrations based on the observed effect, not as a reconstruction of the original trial design. They are not observed power.

For time-to-event outcomes, the stated convention is total number of events; the posted planning illustrations are for other outcomes and are expressed as participants per arm. These calculations do not incorporate every possible trial-design feature, and the registry record does not report the original design’s assumptions.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -0.790; pooled standard deviation σ = 8.707.
2. n = 2 × (1.96 + 0.842)² × 8.707² / -0.790² = 1,907.0, rounded up to 1,907 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 <- -0.79                      # observed difference in means
sigma <- 8.70723279686052                     # 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(2438826)
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 = 1,907 (80% power), 2,553 (90% power)
 75% of observed effect: n per arm = 3,391 (80% power), 4,539 (90% power)
 50% of observed effect: n per arm = 7,628 (80% power), 10,212 (90% power)
power.t.test: 1907.9 
Simulated power at n = 1,907 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 registry analysis is a mixed-model analysis of the primary endpoint. It reports a least-squares mean difference of -0.80, a 95% confidence interval from -2.77 to 1.17, and p = 0.334. This is the trial’s reported model-based comparison and is the appropriate result to foreground when describing the registered primary analysis.

The recalculated comparison uses the posted group summary statistics and yields a mean difference of -0.79, a 95% confidence interval from -3.008 to 1.428, and an unadjusted p-value of 0.485. It is a simple, unadjusted re-calculation rather than a reproduction of the mixed model. The calculations do not flag a discrepancy between the estimates, but the analyses have different methods and need not return identical uncertainty estimates or p-values.

The re-calculation can be useful as a transparent cross-check of the direction and broad scale of the result. It cannot substitute for the sponsor’s model, which accounts for repeated measures and the listed fixed effects. Neither result shows a confidence interval excluding zero. The registry record does not provide the full model implementation details needed to independently reproduce the sponsor’s analysis from the posted summaries alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome and multiple secondary outcomes and analyses. Testing many outcomes or contrasts can increase the chance of obtaining at least one small p-value by chance. Statistical plans may address this with a prespecified hierarchy, adjustment procedure, or other strategy. Whether such a strategy was used, and what it involved, are not reported in the registry record. Accordingly, the secondary p-values should not be interpreted as if each were the only test conducted.

The posted primary analysis population is defined as randomized participants who received at least 1 dose of study drug and had baseline and at least one post-baseline value. This describes who was included in that primary outcome analysis. It is not the same as an intention-to-treat population definition that necessarily includes every randomized participant, and the registry record does not describe a broader analysis set for this endpoint.

The diary-based outcome relies on repeated observations. Some participants may have incomplete diary data or missing assessments, but the number and pattern of missing observations and the reasons for missingness are not reported in the registry record. The registry does not describe the missing-data assumptions, imputation approach, or sensitivity analyses for the primary outcome. Because missingness can affect repeated-measures estimates, those details would help readers assess robustness.

The description identifies a mixed model repeated measures analysis and its listed fixed effects, but not every implementation choice. Details such as the covariance structure, degrees-of-freedom method, and sensitivity to alternative missing-data assumptions are not reported in the registry record. These reporting gaps limit independent assessment; they do not by themselves show that the analysis is invalid.

Likewise, interim analyses, stopping rules, and the original sample-size rationale are not reported in the registry record. The planning illustrations associated with posted effects should not be mistaken for those original design decisions.

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: cluster headache (1.8%), small intestinal obstruction (1.1%), kidney rupture (1.1%), pituitary tumour (1.1%), ureterolithiasis (1.1%).

The registry reports serious adverse event counts separately by treatment phase and group. During the double-blind treatment phase, serious adverse events were reported for 3 of 120 participants in the placebo group and 2 of 117 in the galcanezumab 300 mg group. In the open-label treatment phase, the corresponding listed counts were 11 of 116 for participants described as placebo/GMB 300 mg and 10 of 113 for participants described as GMB 300 mg/GMB 300 mg. The record also lists post-treatment phase groups, with zero serious adverse events among the groups of 2, 4, and 93, and 5 among the group of 93 for GMB 300 mg/GMB 300 mg.

These are descriptive counts within registry-defined groups and phases. Open-label and post-treatment groups should not be treated as directly comparable with the randomized double-blind groups without accounting for their different treatment histories and populations. Serious adverse event counts do not establish that an event was caused by study treatment. The registry also lists zero deaths in each reported group.

The serious events listed most often include Cluster headache at 1.8%, followed by Small intestinal obstruction, Kidney rupture, Pituitary tumour, Ureterolithiasis, and Pregnancy of partner at 1.1% each. The registry record does not provide the information needed to infer causality from these terms or percentages. Safety summaries should be read as reported events, not as proof of treatment effect or absence of risk.

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

The primary result estimates the average difference between galcanezumab 300 mg and placebo in change from baseline in weekly cluster headache attack frequency during the double-blind treatment phase. The reported estimate is -0.80 attacks per week, with a 95% confidence interval from -2.77 to 1.17. The interval includes zero, so the result does not establish a clear between-group difference under the reported analysis.

That conclusion is not the same as saying the treatments are equivalent or that no effect exists. An interval that crosses zero can be compatible with a range of differences in either direction. The trial’s posted result therefore leaves uncertainty about the size and direction of the true average difference. The point estimate should not be treated as a precise prediction for an individual participant.

The endpoint measures an average over repeated diary observations. It does not describe every participant’s response, nor does it show the distribution of changes in the two groups. Secondary response measures provide additional descriptions, but their multiplicity and non-uniform patterns limit their ability to settle the primary question independently.

The safety record reports serious adverse events by phase and group, but event counts alone cannot determine causation. The open-label and post-treatment records also reflect different study phases and treatment histories from the double-blind comparison.

These findings apply to the recorded study population, analysis definition, treatment regimen, and follow-up described in the registry. They do not establish outcomes beyond the reported period or resolve all questions about missing data, model assumptions, or clinical importance. The statistics describe the evidence in the registry record; they are not medical advice.

18. Why This Trial Matters Statistically

This trial illustrates why an estimated effect, its confidence interval, and the analysis method need to be considered together. The primary point estimate is in a direction favoring a larger reduction in weekly attack frequency with galcanezumab, but the confidence interval includes zero and values on both sides. Reporting the point estimate alone would overstate how decisively the data distinguish the groups.

It also illustrates the importance of understanding what an adjusted repeated-measures result represents. The registry’s least-squares mean difference comes from a model that accounts for repeated observations and listed covariates. A simple re-calculation from summary statistics is useful as a check, but it is not a substitute for the model-based analysis. Different methods can produce somewhat different estimates of uncertainty.

The secondary outcomes and safety summaries show why a trial should be read as a connected body of evidence rather than as a collection of isolated p-values or counts. Multiple endpoints can produce varied patterns, and without a reported multiplicity plan, secondary findings require restraint. Safety counts also need their phase and group context, and cannot establish causality by themselves.

Finally, planning illustrations based on an observed effect are not the same as the study’s original sample-size justification or evidence of observed power. Separating planning assumptions from the trial’s actual design record helps avoid retrospective claims that the study was necessarily powered to detect a particular effect.

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 description does not report the original sample-size justification or the trial’s design assumptions. The separate planning illustrations use the observed effect and stated planning assumptions, but cannot show what effect the original design was intended to detect.

The primary analysis population excludes randomized participants who did not receive at least 1 dose or lacked the required baseline or post-baseline value, according to the posted definition. The registry record does not provide a full account of participants excluded from each outcome analysis or the reasons for missing observations. It also does not describe the missing-data assumptions or sensitivity analyses.

The model description names the mixed model repeated measures approach and fixed effects, but does not report every implementation detail. The covariance structure and some other analytic choices are not reported in the registry record, limiting independent reproduction of the sponsor’s result from the posted summary statistics.

The record includes an open-label extension and post-treatment safety groups. These later-phase records do not have the same randomized, blinded comparison as the primary treatment phase and should not be read as equivalent comparative evidence. Their participants also have different treatment histories.

Multiple secondary outcomes are posted, while multiplicity handling and a complete testing hierarchy are not reported in the registry record. This makes isolated secondary findings less conclusive. Finally, the primary outcome is an average change measure and does not provide the distribution of individual responses or directly establish the clinical importance of the observed estimate.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Galcanezumab in Participants With Chronic Cluster Headache — NCT02438826.
• Registry record last updated 2020-08-25; status last verified 2020-06.
• Results first posted 2019-06-11.
• 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 study of galcanezumab 300 mg versus placebo in participants with chronic cluster headache. The double-blind treatment phase lasted 3 months, and the study included a long-term open-label extension.

The primary outcome was overall mean change from baseline in weekly cluster headache attack frequency, analyzed using mixed models for repeated measures. The reported least-squares mean difference was -0.80 attacks per week, with a 95% confidence interval from -2.77 to 1.17 and p = 0.334. The interval includes zero, leaving uncertainty about the direction and size of the average between-group difference.

The record also posts secondary outcomes and adverse event summaries. Multiplicity handling, detailed missing-data methods, and the original sample-size justification are not reported in the registry record. Planning illustrations based on observed effects are separate from the study’s original design rationale.