A Safety Study of Galcanezumab in Participants With Migraine, With or Without Aura: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Safety Study of Galcanezumab in Participants With Migraine, With or Without Aura (NCT02614287), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Discontinued Due to Adverse Event.

2. Clinical Question

The registry describes the study’s main purpose as evaluating longer-term safety in participants with episodic or chronic migraine. The posted primary outcome focuses on one safety-related event: stopping study treatment due to an adverse event. The groups’ results therefore address discontinuation under these two galcanezumab regimens, rather than a comparison of galcanezumab with no treatment or another medicine.

The study also listed outcomes involving drug concentrations, calcitonin gene-related peptide, anti-drug antibodies, migraine and headache days, acute medication use, and the proportion with a specified reduction in monthly migraine headache days. These outcomes provide additional kinds of information, but they do not change the primary safety question. The registry record does not report a primary efficacy question or a formal superiority objective for migraine outcomes.

3. Trial Design

This was a Phase 3, randomized, parallel-group, open-label study sponsored by Eli Lilly and Company. The registry lists an enrollment of 270 and a completed status. The study began on 2015-11-30, and primary completion was recorded as 2017-05-12. Participants were assigned to one of two galcanezumab dosing regimens; there was no placebo group.

In the 120 mg group, participants received a 240 mg loading dose at the first dosing visit, followed by 120 mg once a month for up to 11 months. In the 240 mg group, participants received 240 mg once a month for up to 12 months. Both regimens used subcutaneous injections, with an auto injector or pre-filled syringe listed as delivery options. The groups thus differed in their planned ongoing monthly dose as well as in the loading-dose schedule.

Because the study was open-label, treatment assignment was not masked. That design matters when interpreting outcomes involving participant or investigator reporting, decisions to discontinue, or clinical assessment. Randomization can support a comparison between assigned groups, but it does not remove all possible effects of awareness of treatment assignment. The registry record does not report details of the randomization procedure or allocation concealment.

For the primary adverse-event analysis, the registry describes the population as randomized participants who received at least one dose. It also notes that 6 participants in the 120 mg group discontinued after receiving a 240 mg loading dose and were moved to the 240 mg group for adverse-event analysis. The posted primary group denominators are 129 and 141. The record does not report the original trial design assumptions for sample size, nor does it report a rationale for the number enrolled.

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.

Open Label (OL) Treatment Phase

Reasons for not completing this period:

Post Treatment Follow-up 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 one dose of study drug. There were 6 participants in the 120 mg group who discontinued after receiving loading dose of 240mg, these participants were moved to 240mg group for AE analysis.

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

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Discontinued Due to Adverse Event, measured over Baseline through Month 12.

The primary endpoint is the percentage of participants who discontinued due to an adverse event from baseline through Month 12. The registry defines an adverse event as an untoward medical occurrence after a pharmaceutical product is administered, whether or not it is considered related to treatment. It may include an unfavorable sign, symptom, disease, or abnormal laboratory finding temporally associated with product use.

This endpoint captures a particular consequence of safety and tolerability: stopping study treatment because of an adverse event. It does not count every adverse event, measure how severe each event was, or establish that treatment caused an event. A participant can experience an adverse event without discontinuing, while discontinuation reflects an event and a decision to stop treatment. The registry’s description also directs readers to the Adverse Events section for other non-serious adverse events and all serious adverse events, regardless of causality.

In the posted results, 4.65% of participants in the 120 mg group and 4.96% in the 240 mg group discontinued due to an adverse event. Those percentages describe the recorded endpoint in the analyzed groups; they should not be read as a complete safety profile or as a direct measure of comparative migraine benefit. The endpoint is useful for describing one treatment-limiting aspect of safety over the stated follow-up, but the registry record does not report a broader composite safety endpoint as primary.

7. Results Posted in the Registry

• Galcanezumab 240 mg: 5.0% (7/141) versus 4.7% (6/129) on control; risk difference 0.3 percentage points (95% CI -4.8 to 5.4), risk ratio 1.07 (0.37–3.09); unadjusted two-proportion z-test p = 0.904.

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.

Serum Concentrations of Galcanezumab

• 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 deviations.
• Result:
  • Galcanezumab 240 mg: mean 31,600 versus 16,500 on control; difference 15,100 (95% CI 10,994 to 19,206), standardized effect d = 1.15; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Galcanezumab 240 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Plasma Concentration of Calcitonin Gene-Related Peptide (CGRP)

• 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 deviations.
• Result:
  • Galcanezumab 240 mg: mean 3.85 versus 2.74 on control; difference 1.11 (95% CI 0.69 to 1.53), standardized effect d = 0.72; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Galcanezumab 240 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Developing Anti-Drug Antibodies to Galcanezumab

• 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 240 mg: 7.3% (10/137) versus 12.4% (16/129) on control; risk difference -5.1 percentage points (95% CI -12.3 to 2.1), risk ratio 0.59 (0.28–1.25); unadjusted two-proportion z-test p = 0.161.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Galcanezumab 240 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several domains rather than a single confirmatory question. They include pharmacokinetic measures, serum and plasma concentrations, anti-drug antibodies, migraine and headache days, a responder threshold for monthly migraine headache days, and acute medication use. This breadth means that the results are not all measuring the same construct, and a pattern across them should not be reduced to one summary claim.

The posted Month 12 concentration comparisons have recalculated confidence intervals above zero, while the anti-drug antibody risk-difference interval includes zero. The registry also lists migraine-related endpoints, but the record does not provide a basis for treating the secondary findings as a single prespecified efficacy conclusion. The primary result concerns discontinuation due to adverse events; secondary biological or migraine-related measures do not replace that safety endpoint or directly explain it.

Unadjusted secondary results carry less weight when many outcomes are examined. Each additional comparison creates more opportunity for a seemingly notable result to arise by chance, even if no underlying difference exists. The registry record does not report a multiplicity adjustment or a hierarchy assigning confirmatory status to the secondary analyses. It also does not report a complete analysis plan for those outcomes. Therefore, nominal p-values and confidence intervals should be read as exploratory evidence, not as definitive confirmation across the range of outcomes.

Differences in available group sizes across endpoints further caution against assuming that every comparison represents the same participants or has the same precision. The secondary results can help describe what was measured and identify questions for further study, but they should be interpreted alongside their endpoint definitions, timeframes, analysis populations, and uncertainty. They do not alter the central finding that the primary endpoint comparison was imprecise and did not establish a difference between the two dosing regimens.

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

• Pharmacokinetics (PK): Area Under the Concentration Time Curve (AUC) of Galcanezumab
• Serum Concentrations of Galcanezumab
• Plasma Concentration of Calcitonin Gene-Related Peptide (CGRP)
• Percentage of Participants Developing Anti-Drug Antibodies to Galcanezumab
• Overall Mean Change From Baseline in the Number of Migraine Headache Days (MHD)
• Overall Mean Change From Baseline in the Number of Headache Days
• Percentage of Participants With Overall Reduction From Baseline ≥50% in Monthly Migraine Headache Days
• Overall Mean Change From Baseline in the Frequency of Medication Use for the Acute Treatment of Migraines or Headaches

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: a participant either discontinued due to an adverse event during the stated timeframe or did not. The registry reports percentages by group and an analysis using Fisher Exact. A recalculation also expresses the comparison as a risk difference, which is the event proportion in one group minus the event proportion in the reference group. The recalculated estimate is unadjusted: it compares the posted group summaries without adjustment for other variables.

What does a risk difference describe?

A risk difference expresses the absolute separation between two event proportions on the probability scale. A value of zero corresponds to equal proportions. A positive or negative value indicates the direction of the difference according to the comparison’s specified group order. Unlike a relative measure, an absolute difference keeps the comparison tied to the observed event probabilities. The estimate should be read with its confidence interval, since a point estimate alone does not show how uncertain the comparison is.

Why is Fisher Exact used?

Fisher Exact is a method for testing association in a two-group binary outcome using the observed counts. It is often used when event counts are limited, because its calculation does not rely on the same large-sample approximation used by some other tests. The registry reports this method for the primary comparison and for the anti-drug antibody comparison. The registry record does not report further details about the test specification, such as whether the test was one-sided or two-sided.

The recalculated risk difference and its confidence interval are simple unadjusted calculations from the posted summary statistics. They are not a replacement for the sponsor’s own analysis. The registry’s reported p-value is p=1 for the primary endpoint, while the recalculated unadjusted p-value is 0.904. The registry record does not identify the reason for the difference between these reported p-values. The comparison should therefore be interpreted with the registry’s own analysis in view, rather than treating the recalculation as a substitute.

How do the continuous outcomes differ?

For the Month 12 concentration outcomes, the registry reports group means and standard deviations. A mean difference compares the average measurements between groups. The standard deviation describes variation among individual measurements around the group mean; it is not the uncertainty in the mean itself. The recalculated confidence intervals quantify uncertainty in the mean differences under the calculation’s assumptions. A confidence interval that lies entirely on one side of zero indicates that the interval does not include a zero difference, but it does not by itself establish clinical importance or remove concerns about multiple comparisons.

Standard errors, when reported in the recalculation, describe the estimated uncertainty of each group mean. They are distinct from standard deviations: standard errors concern precision of the mean estimate, whereas standard deviations describe spread of observations. The record reports standard deviations for both Month 12 concentration outcomes. No adjusted estimates or covariate-adjusted analysis results are reported for these comparisons.

What do p-values and confidence intervals contribute?

A p-value measures how compatible the observed data are with a specified null hypothesis under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of a difference. A confidence interval gives a range of estimates compatible with the data and method at its stated confidence level. For a difference, whether the interval includes zero is relevant to statistical evidence for a nonzero difference, while the interval’s breadth helps convey precision.

The posted analyses include both registry-reported tests and recalculated comparisons. The recalculations are unadjusted and should be understood as descriptive comparisons based on summary data. The registry record does not report a comprehensive statistical analysis plan, model specifications, prespecified covariate adjustments, or detailed handling of repeated measurements. The record does not report whether analyses were conducted according to an intention-to-treat principle for every outcome.

The primary analysis population is described as randomized participants who received at least one dose. This is not the same as automatically analyzing every randomized participant in the originally assigned group: the registry specifically says that 6 participants who received a 240 mg loading dose before discontinuing from the 120 mg group were moved to the 240 mg group for adverse-event analysis. That detail is important for understanding the posted denominators and the basis of the safety comparison. The record does not report how missing outcome values were handled, or whether any sensitivity analyses assessed their effect.

Several secondary outcomes involve proportions, others involve continuous measurements, and migraine-related outcomes involve changes or response thresholds. These outcome types answer different questions and may have different analysis populations or data requirements. The registry record lists the outcomes but does not report a full multiplicity strategy or all analysis details for them. Consequently, the posted results support description of the measured outcomes, but they do not justify assuming that every analysis was prespecified, adjusted, or based on the same set of participants.

11. Confidence Intervals and Precision

Precision is about how narrowly an estimate is determined by the observed data and the method used. A confidence interval communicates this uncertainty by giving a range of values compatible with the data under the calculation’s assumptions. It does not guarantee that the true effect lies within that range, and it does not account for sources of bias that are not represented in the calculation.

For the primary discontinuation comparison, the recalculated risk difference was 0.003, with a 95% confidence interval from -0.048 to 0.054. Because the interval crosses zero, the posted summary data do not pin down the direction of the difference. Its endpoints also show that the data are compatible with a range of possible differences, not only the small point estimate. The corresponding unadjusted recalculated p-value was 0.904, while the registry’s Fisher Exact analysis reports p=1.

The confidence intervals for the two Month 12 concentration comparisons lie above zero: the serum galcanezumab mean difference was 15100, with an interval from 10990 to 19210; the plasma CGRP mean difference was 1.11, with an interval from 0.688 to 1.532. For anti-drug antibodies, the recalculated risk difference was -0.051, with an interval from -0.123 to 0.021, which includes zero. These intervals describe statistical uncertainty in the stated comparisons, not clinical significance.

Precision is also affected by the number of observations available for an outcome. The registry reports different group sizes across outcomes, including the Month 12 measurements, and does not report a complete account of missing values or their handling. Thus, a reader should not assume the same analysis population or precision applies to every endpoint. Confidence intervals based on posted summary values also cannot address open-label design, outcome selection, or other possible sources of systematic error.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations are planning calculations based on the observed effect, not the trial’s original design. For these non-time-to-event outcomes, the figures mean participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that a hypothetical future study would need, under those assumptions, to have an 80% chance of detecting the specified effect if that effect were true. The 90% power column uses a higher target probability of detecting that effect. Neither column says how likely the observed result is to be true. These calculations are not observed power.

Each planning row uses a different fraction of the effect observed in the posted comparison. Planning for 100% of the observed effect assumes the full observed separation is worth detecting; planning for 75% or 50% assumes a smaller target effect. Smaller effects are harder to distinguish from sampling variation, so they require more participants for the same target power. The resulting figures can be very large when the observed difference is small or uncertain.

These are illustrations, not evidence that the completed trial was adequately or inadequately sized. They inherit the uncertainty of the observed effect and rely on the stated simplified assumptions. They do not account for design features or analytic choices that are not reported in the registry record, and they should not be interpreted as a reconstruction of the sponsor’s original planning.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.047; treatment proportion p₁ = 0.050; average p̄ = 0.048.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3025 = 0.5930.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3025 = 0.2546.
4. n = (0.5930 + 0.2546)² / (0.0031)² = 73,156.1, rounded up to 73,157 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.0465116279069767                          # control proportion
p1 <- 0.049645390070922                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2614287)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 73,157 (80% power), 97,935 (90% power)
 75% of observed effect: n per arm = 129,050 (80% power), 172,761 (90% power)
 50% of observed effect: n per arm = 288,097 (80% power), 385,680 (90% power)
power.prop.test: 73156.1 
Simulated power at n = 73,157 per arm: 0.801 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison as a Fisher Exact analysis with p=1. The unadjusted recalculation from the posted event counts gives a risk difference of 0.003, a 95% confidence interval from -0.048 to 0.054, and p=0.904. The two p-values are close in their implication that the primary comparison does not provide evidence of a difference under conventional testing, but they are not identical.

The registry record does not report why the p-values differ or provide additional test details that would permit a full reconciliation. The recalculation is a simple unadjusted analysis based on the posted summary statistics; it is not an adjusted or participant-level analysis. The registry’s own analysis should be regarded as the sponsor-reported result, while the recalculated estimate and interval offer an additional description of the contrast and its uncertainty.

For the anti-drug antibody outcome, the registry reports a Fisher Exact p-value of .215, while the unadjusted recalculation reports the unadjusted p-value 0.161. The record does not explain this difference either. The other displayed secondary comparisons have no sponsor-reported analyses listed. These distinctions matter: a recalculated result can help readers understand the size and precision of a comparison, but it cannot establish that it reproduces every detail of the sponsor’s analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 14 outcome measures and 12 analyses, including multiple secondary outcomes. When many statistical comparisons are made, the chance of at least one nominally unusual result can increase. A multiplicity strategy may control that risk through prespecified methods, such as adjusting significance thresholds or defining an order for testing. The registry record does not report whether such a strategy was used for the posted results, nor does it identify a hierarchy that distinguishes confirmatory from exploratory secondary outcomes. Secondary p-values should therefore be interpreted cautiously.

Missing data are another source of uncertainty. The record gives outcome-specific group sizes for several results, but it does not provide a full accounting of missing observations, reasons for missingness, or the methods used to handle missing values. It does not report sensitivity analyses evaluating how alternative assumptions about missing data might affect the results. Without those details, it is not possible to assess whether missingness could have influenced particular comparisons.

The primary population is described as all randomized participants who received at least one dose of study drug. The registry also states that 6 participants in the 120 mg group who discontinued after receiving a 240 mg loading dose were moved to the 240 mg group for adverse-event analysis. That is a specific safety-analysis assignment rule, and it means the posted analysis should not automatically be interpreted as a strict comparison by original randomized group. The registry record does not report whether other outcomes used the same population or grouping rule.

Details of the statistical analysis plan, covariate adjustment, handling of repeated measurements, and sensitivity analyses are not reported in the registry record. These omissions limit assessment of how prespecified the analyses were and how robust the results are to alternative methods. They do not invalidate the posted numbers, but they narrow the conclusions that can be drawn from them.

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: haemorrhagic ovarian cyst (1.1%), endocarditis (0.9%), infective aneurysm (0.9%), subarachnoid haemorrhage (0.9%), lung neoplasm malignant (0.9%).

The serious adverse-event listings report affected participants separately for the open-label and post-treatment phases. During the open-label phase, the registry lists serious adverse events for 3 of 129 participants in the 120 mg group and 7 of 141 in the 240 mg group. During the post-treatment phase, it lists 3 of 112 and 2 of 124, respectively. The registry lists zero deaths in each of these groups.

These figures are not the primary endpoint. The primary endpoint counts participants who discontinued due to an adverse event; serious adverse-event figures describe a separate safety category. The registry’s primary endpoint definition also states that an adverse event need not have a causal relationship with treatment. Serious adverse-event counts should therefore be read as reported events in the relevant group and phase, not as proof that the study drug caused them.

The record lists several serious-event terms with percentages, including haemorrhagic ovarian cyst, endocarditis, infective aneurysm, subarachnoid haemorrhage, lung neoplasm malignant, and uterine leiomyoma embolisation. These listings describe reported terms, but the record does not establish causal attribution for each event. The study’s open-label design, group sizes, and lack of a placebo group also limit how much can be inferred from between-group differences in these counts.

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

The primary result describes discontinuation due to an adverse event in two galcanezumab dosing groups over the stated timeframe. The posted percentages were 4.65% for the 120 mg group and 4.96% for the 240 mg group. The recalculated risk difference is close to zero, but its confidence interval includes zero and extends in both directions. The registry’s Fisher Exact analysis reports p=1. Together, these results do not establish a difference in this endpoint between the regimens.

That conclusion is narrower than saying the treatments are equivalent or that their safety profiles are identical. Equivalence requires a prespecified margin and an analysis designed to assess whether differences fall within that margin; the registry record does not report such a design. A lack of statistically significant evidence for a difference is not proof that no difference exists. The confidence interval indicates that the estimated contrast is uncertain.

The endpoint also does not answer whether galcanezumab is better than placebo, because there was no placebo group. Nor does it measure migraine prevention directly. Migraine-related outcomes appear among the secondary outcomes, but their presence does not make the primary safety result evidence of clinical benefit. The open-label design may also affect reporting and discontinuation decisions, and the record does not report methods that would quantify or remove those effects.

Adverse events, serious adverse events, discontinuations due to adverse events, drug concentrations, antibodies, and migraine measures are distinct outcomes. None should be used as a substitute for another. The record’s adverse-event definition allows events without established causal relation to treatment, so reported events should not automatically be attributed to galcanezumab.

The study contributes descriptive information about longer-term use under the two dosing schedules and the outcomes recorded in this trial. It does not settle broader questions about safety in populations or settings not described in the record, and it does not establish a general absence of risk. The most defensible reading is specific to the posted comparison, endpoint, follow-up period, and analysis population.

18. Why This Trial Matters Statistically

This trial illustrates why an endpoint’s meaning and a comparison’s precision matter as much as a p-value. The primary outcome is not all adverse events, but discontinuation attributed to an adverse event. The posted group percentages are close, yet the recalculated confidence interval spans zero and a range of differences in either direction. A single point estimate or non-significant test cannot establish that the regimens are equivalent.

The study also shows why design details affect interpretation. Participants were randomized, but the trial was open-label and lacked a placebo group. In addition, the registry describes moving 6 participants who received a 240 mg loading dose to the 240 mg group for adverse-event analysis. These features help define what the comparison represents and caution against reading it as a simple comparison by original assignment or as a comparison with no treatment.

Finally, the registry lists many secondary outcomes across safety, pharmacokinetics, biomarkers, and migraine measures. Such breadth can be informative, but it also raises questions about multiplicity, analysis populations, and missing data. The record does not report a full statistical analysis plan or multiplicity approach. The trial is therefore a useful example of separating the primary safety result from exploratory secondary patterns and of giving uncertainty and reporting limitations a central role in interpretation.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The study was open-label, and the registry record does not report masking of participants or study personnel. Awareness of treatment assignment can influence subjective reporting, clinical decisions, and discontinuation. The comparison was between two galcanezumab regimens, with no placebo group, so it cannot estimate the effect of galcanezumab versus no treatment from this comparison alone.

The primary safety analysis used a population of randomized participants who received at least one dose, and the registry notes that 6 participants were moved from the 120 mg group to the 240 mg group for adverse-event analysis after receiving a 240 mg loading dose. This makes the analysis grouping important to interpretation. The registry record does not report enough detail to assess whether other outcomes used the same population or how assignment was handled in all analyses.

The record does not report the trial’s original sample-size assumptions, a complete statistical analysis plan, a multiplicity strategy, detailed missing-data methods, or sensitivity analyses. Outcome-specific group sizes vary, and the record does not provide a complete explanation for missing observations. These gaps constrain assessment of precision and robustness, particularly for the secondary outcomes.

The study’s primary endpoint captures discontinuation due to an adverse event, not the full range, severity, or causal attribution of adverse events. The listed serious adverse events are separate safety summaries and do not establish causation. Generalizability beyond the enrolled migraine population and the studied dosing schedules is not established by the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Safety Study of Galcanezumab in Participants With Migraine, With or Without Aura — NCT02614287.
• Registry record last updated 2020-06-17; status last verified 2020-06.
• Results first posted 2019-01-07.
• 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 NCT02614287 as a completed Phase 3, randomized, parallel-group, open-label safety study sponsored by Eli Lilly and Company. It enrolled 270 participants with migraine, with or without aura, and compared two galcanezumab dosing regimens. The primary outcome was the percentage who discontinued due to an adverse event from baseline through Month 12.

The posted primary percentages were 4.65% for the 120 mg group and 4.96% for the 240 mg group. The registry reports a Fisher Exact p-value of 1; the unadjusted recalculation gives a risk difference of 0.003, with a 95% confidence interval from -0.048 to 0.054. The results do not establish a difference in the primary endpoint.

The record also lists secondary safety, concentration, antibody, and migraine-related outcomes. Multiplicity procedures, full missing-data methods, and the original sample-size assumptions are not reported in the registry record, limiting how firmly secondary patterns and broader conclusions can be interpreted.