Non-Invasive Neurostimulation for the Prevention of Chronic Migraine: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Non-Invasive Neurostimulation for the Prevention of Chronic Migraine (NCT01667250), a randomized na study. The primary outcome is Safety - Number of Participants With Adverse Events.

2. Clinical Question

3. Trial Design

The registry describes a multi-center, prospective, double-blind, randomized, sham-controlled pilot study of non-invasive vagal nerve stimulation with the GammaCore device for chronic migraine prevention. The study used a parallel-group model, comparing the GammaCore Active Device with the GammaCore Sham Device. Its stated purpose included studying feasibility, collecting preliminary clinical data related to safety and clinical benefits, and supporting development and approval of a larger pivotal study.

The registry lists enrollment as 59 and the status as completed. The recorded study start is 2012-10, and primary completion is 2014-05. The phase is listed as NA. The sponsor is ElectroCore INC. Additional information about the number or location of study centers, the randomization sequence, allocation concealment, and the masking procedures is not reported in the registry record.

The randomized period was described as lasting up to 8 weeks for the primary safety outcome. The active arm is described as using an active GammaCore device. The sham arm description states that subjects using the sham device in Phase 2 would receive active GammaCore treatment during Phase 3 of the study. More detail about how that sequence relates to the randomized comparison, or how participants were followed across phases, is not reported in the registry record.

The posted primary endpoint is a participant count for adverse events in the randomized population. Secondary outcomes listed in the registry include mean change in headache days, headache days by peak severity, use of pain-relief medication, and mean change in the SF-12 quality-of-life survey. Numerical secondary results are posted for mean change in headache days; results for the other listed secondary outcomes are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Run-in (no Treatment)

Randomised Period

Analysis population for the primary outcome, as defined in the registry: Randomized population

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: Randomized population

6. Primary Endpoint

The registry lists the primary outcome as Safety - Number of Participants With Adverse Events, measured over Up to 8 weeks - duration of the Randomized period.

The primary endpoint is the number of participants with adverse events during the randomized period, described as lasting up to 8 weeks. The registry says safety was assessed by collecting adverse effects and identifies the analysis population as the randomized population. The endpoint is a count of participants, so it records whether a participant was counted as having an adverse event rather than the number, duration, or severity of events experienced by each participant.

A participant-count safety endpoint is useful for describing how many people in each randomized group had at least one event under the registry’s outcome definition. It provides a direct summary of the frequency of participants affected in each arm. It does not, by itself, characterize event seriousness, the relationship of an event to treatment, or whether a participant experienced more than one event. Those details require separate outcome information.

The posted primary results are 6 participants in the active-device arm and 5 in the sham-device arm, with arm sizes of 30 and 29, respectively. The registry also posts a risk-difference estimate and its confidence interval. The primary endpoint is specifically a safety measure; it does not directly measure headache-day change, pain-relief medication use, or quality of life. Those are separate outcomes and should not be treated as interchangeable with the adverse-event count.

The registry record does not report a more detailed operational definition of an adverse event, the method for attributing events to treatment, or whether event severity was part of the primary endpoint definition. The separate serious-adverse-event information can add context, but it does not change the primary endpoint’s stated focus on participants with adverse events.

7. Results Posted in the Registry

• GammaCore Active Device: 20.0% (6/30) versus 17.2% (5/29) on control; risk difference 2.8 percentage points (95% CI -17.1 to 22.6), risk ratio 1.16 (0.40–3.39); unadjusted two-proportion z-test p = 0.786.

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.

Mean Change in Headache Days

• 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:
  • GammaCore Active Device: mean -1.50 versus -0.20 on control; difference -1.30 (95% CI -3.82 to 1.22), standardized effect d = -0.27; z-test p = 0.312.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GammaCore Active Device and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists four secondary outcome measures: mean change in headache days, headache days by peak severity, use of pain-relief medication, and mean change in the SF-12 quality-of-life survey. Numerical arm summaries and a comparison are posted for mean change in headache days. Numerical results for the other listed secondary outcomes are not reported in the registry record, so the overall pattern across the full set cannot be assessed.

The headache-day outcome concerns symptom frequency and is distinct from the primary safety endpoint, which counts participants with adverse events. Its posted estimate is a between-arm mean difference, and its uncertainty is substantial: the confidence interval includes zero. This provides a separate, preliminary description of headache-day change; it neither explains nor replaces the primary safety result. A safety comparison and a symptom-frequency comparison answer different questions.

Secondary outcomes can help describe dimensions of a trial beyond its primary endpoint, but they generally carry less confirmatory weight when multiple outcomes are examined and no hierarchy or adjustment is reported. The registry record does not report a multiplicity strategy, a prespecified order for interpreting secondary measures, or analyses for the other listed outcomes. Any unadjusted secondary finding should therefore be treated as exploratory rather than as independent confirmation of a primary result.

The posted secondary information also does not establish a consistent overall effect across headache frequency, severity, medication use, and quality of life. Such a claim would require results across those domains and a clear plan for interpreting them together. With results absent for several listed outcomes and analysis details not reported, the secondary data offer limited scope for an integrated assessment.

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

• Mean Change in Headache Days
• Total Number of Headache Days Per Arm With Peak Severity of Mild, Moderate, or Severe
• Use of Pain Relief Medication
• Mean Change in Quality of Life Short Form Survey (SF-12)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

The primary endpoint is binary at the participant level: a participant is counted as having an adverse event or not, according to the outcome definition. A risk difference expresses the difference between the proportions of participants with the event in the two arms. Unlike a relative measure, it is expressed on the probability scale and can be positive or negative, depending on which group has the greater observed event risk and on the subtraction order. The registry identifies the comparison as active device versus sham device and posts a risk difference of 0.028.

The arm-level counts and sizes describe the data used for the comparison: 6 of 30 in the active arm and 5 of 29 in the sham arm. The posted estimate, rather than an independently derived calculation, is the comparison result to interpret. The registry’s reported analysis is the primary reference for the trial result. The interval around the risk difference communicates how uncertain the estimate is under the analysis method; it is not a range containing a known, fixed percentage of individual participant outcomes.

How do relative measures differ?

A risk ratio compares the risk in one arm with the risk in the other. An odds ratio compares the odds of an event rather than the risks themselves. The registry posts a risk ratio of 1.16 and an odds ratio of 1.2, each with its own confidence interval. These measures can appear numerically different because they use different scales. They should not be read as additional independent evidence: they summarize the same outcome and the same arm comparison using different effect measures.

Relative estimates can be harder to interpret without the underlying event frequency. For that reason, it is useful to read them alongside the observed counts and the absolute risk-difference estimate. Neither a relative measure nor an absolute measure eliminates uncertainty in a small pilot comparison. The intervals reported for the relative measures span the value representing no relative difference, as does the interval for the risk difference on its scale.

What does the p-value address?

The registry posts an unadjusted p-value of 0.786 for the primary comparison. In general, a p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. It is not the probability that the null hypothesis is true, nor does it measure the probability that a result will be reproduced. It also does not quantify clinical importance or replace the effect estimate and its interval.

The word “unadjusted” matters because the registry lists multiple outcomes. If many hypotheses are tested, the chance of obtaining at least one apparently unusual result can increase. The registry record does not report a multiplicity adjustment or a prespecified testing hierarchy. The posted p-values should therefore be interpreted as unadjusted summaries rather than as evidence that accounts for testing across outcomes.

How should the continuous secondary outcome be read?

Mean change in headache days is a continuous outcome. The registry reports an arm mean and standard deviation for each group, followed by a mean-difference estimate. A mean difference compares average changes between arms; it does not describe every participant’s change or the spread of individual responses. The reported estimate is -1.3, and its confidence interval extends from -3.818 to 1.218. The interval crosses zero, so the data remain compatible with a range that includes no mean difference.

The standard deviations describe variation among participant measurements around each arm mean. They are not confidence intervals and do not directly state how precisely the treatment contrast has been estimated. The contrast’s confidence interval incorporates uncertainty in the comparison. The registry reports an unadjusted p-value of 0.312 for this endpoint, but no reported analysis details beyond the posted summary are available.

Why does over-dispersion matter for count outcomes?

General statistical context: count outcomes can vary more than a simple model assumes. When that happens, over-dispersion can make model-based uncertainty too small if the extra variation is ignored. The primary endpoint is a count of participants with an event, which is a binary outcome summarized by arm, not a count of repeated events per participant. The registry record does not report a model for repeated event counts or an over-dispersion assessment. It would therefore be inappropriate to infer that a particular count model or correction was used.

For the headache-day outcome, the record gives means and standard deviations but does not report a detailed statistical analysis plan, model specification, covariate adjustment, or method for handling repeated measurements. The exact analysis methods beyond the posted estimates are not reported in the registry record. General explanations of common methods cannot establish which method was used in this study.

What can be concluded about the analysis plan?

The record identifies randomization, double masking, a parallel model, the primary endpoint, and the randomized population for that endpoint. It does not report the original statistical analysis plan, how allocation was generated or concealed, the treatment of missing outcome data, or whether interim analyses were planned or performed. The registry lists zero reported analyses. That does not permit an assumption about which unreported tests or analyses may have been conducted outside the registry entry.

The posted estimates should consequently be read as registry results with limited accompanying methodological detail. General statistical principles help explain what the effect estimates and intervals mean, but they do not fill gaps in the trial’s undocumented methods. The pilot purpose also means that the estimates can inform planning and describe the observed data without being treated as a definitive test of a final clinical hypothesis.

11. Confidence Intervals and Precision

Confidence intervals show the range of effect estimates that are reasonably compatible with the observed data under the analysis assumptions. They express uncertainty about a group contrast; they do not show the range of individual participants’ outcomes or guarantee that the true effect lies inside the interval. The width of an interval matters: a wide interval leaves more uncertainty about the magnitude and direction of the contrast than a narrow interval.

For the primary risk difference, the point estimate is 0.028 and the interval runs from -0.171 to 0.226. Because the interval includes zero and extends to either side, it does not pinpoint whether the active arm had a higher or lower event risk than the sham arm. The endpoints also allow materially different possible contrasts, so the estimate is not precise enough to support a narrow account of the group difference.

The relative estimates are similarly uncertain. The risk ratio is 1.16, with an interval from 0.397 to 3.387; the odds ratio is 1.2, with an interval from 0.322 to 4.469. Each interval includes its no-difference value. Changing the effect scale does not remove the uncertainty visible in the data.

For mean change in headache days, the mean difference is -1.3 and the interval runs from -3.818 to 1.218. It includes zero and allows values on both sides of it. The estimate therefore does not determine a precise direction or magnitude of the between-arm difference. The registry does not report confidence intervals for the individual arm means.

These limits on precision are important when interpreting a pilot study. The point estimates are useful descriptions, but the intervals show that substantially different effects remain compatible with the posted summaries. The registry record does not report a target precision or a trial-specific justification for the enrollment size.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the original trial’s documented design assumptions. For these two-arm comparisons, the entries are participants per arm for 80% power and participants per arm for 90% power. They are not total participants across both arms and are not observed enrollment figures. The registry record does not report the trial’s original sample-size justification or its design assumptions.

The planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers the full observed effect and smaller fractions of that observed effect: 100%, 75%, and 50%. The corresponding rows show how the planning requirement changes as the effect to detect is reduced. Smaller effects need more participants because they are harder to distinguish from random variation.

The 80% power column represents the planned chance of detecting the specified effect at the stated significance level if that effect is present and the planning assumptions hold. The 90% column uses a higher target chance of detection under those same assumptions. Neither column reports the probability that the trial’s result is correct, and neither is a measure of the probability that the study found an effect. This is not observed power.

The displayed figures are conditional planning calculations, not evidence that a future study must use those exact enrollment targets. The assumptions may not match a later study’s population, outcome definition, allocation, analysis, or target effect. For the primary binary endpoint, the planning entries are based on the observed risk difference. For mean change in headache days, they are based on the observed mean difference and its reported variation. These calculations illustrate how assumed effect size influences planning; they do not add evidence to the trial’s observed results.

The sample-size assumptions for time-to-event outcomes would use total events, but these posted outcomes are not time-to-event outcomes. The relevant planning figures are therefore participants per arm. The original design’s sample-size assumptions are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.172; treatment proportion p₁ = 0.200; average p̄ = 0.186.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5505 = 1.0790.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5502 = 0.4630.
4. n = (1.0790 + 0.4630)² / (0.0276)² = 3,124.6, rounded up to 3,125 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 <- 0.172413793103448                          # control proportion
p1 <- 0.2                          # 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(1667250)
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 = 3,125 (80% power), 4,183 (90% power)
 75% of observed effect: n per arm = 5,477 (80% power), 7,331 (90% power)
 50% of observed effect: n per arm = 12,142 (80% power), 16,253 (90% power)
power.prop.test: 3124.6 
Simulated power at n = 3,125 per arm: 0.800 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcome measures. The secondary measures cover headache-day change, headache days categorized by peak severity, pain-relief medication use, and SF-12 quality-of-life change. The record does not report a hierarchy for testing these outcomes, a family-wise error strategy, a false-discovery strategy, or any other multiplicity adjustment. The posted p-values are identified as unadjusted. When several outcomes are examined, an unadjusted p-value does not account for the possibility of chance findings across the full set of tests.

The registry lists zero reported analyses. Numerical results are posted for the primary adverse-event endpoint and for mean change in headache days, while numerical results for the other listed secondary measures are not reported in the registry record. It is not possible to infer from the missing results whether an outcome was not measured, was analyzed but not posted, or was omitted for another reason.

The primary endpoint population is identified as the randomized population. The registry does not define whether the analysis followed an intention-to-treat principle, how participants were handled after discontinuation, or whether any exclusions were made. For the secondary headache-day outcome, the reported arm sizes are 29 and 28. Reasons for the difference between those outcome denominators and the primary outcome arm sizes, and the handling of missing measurements, are not reported in the registry record. No missing-data method or sensitivity analysis is described.

The record also does not report whether interim analyses were planned or performed, whether outcome definitions changed, or whether the analyses were prespecified before data were reviewed. These omissions limit the ability to evaluate selective reporting, the influence of missing observations, and the extent to which the posted comparisons reflect an established analysis plan. They do not establish that any particular problem occurred; they mark information that is unavailable in the registry record.

15. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: worsening of headache pain (3.3%), appendicitis (3.3%).

The serious-adverse-event record reports 2 affected participants in the GammaCore Active Device arm and 0 in the GammaCore Sham Device arm. The corresponding numbers at risk are 30 and 29. Deaths are reported as 0 in each arm. These figures describe the serious-event entries in the registry and should be kept distinct from the primary endpoint, which counts participants with adverse events more broadly.

The registry also lists Worsening of Headache Pain and Appendicitis among the top serious terms, each at 3.3%. The term-level percentages should not be treated as a complete account of all serious events or as evidence about causation. The record does not report further detail on event timing, severity criteria, relatedness to the device, or how multiple events in the same participant were handled.

The separate other-adverse-event figures are 6 affected participants in the active arm and 5 in the sham arm, with 30 and 29 at risk. The registry does not explain overlap between serious and other adverse-event categories. These summaries describe reported counts; they do not by themselves establish whether the devices caused an event or provide a full assessment of safety.

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

The primary result is a preliminary comparison of participants with adverse events during a randomized period lasting up to 8 weeks. The posted risk difference is 0.028, and its confidence interval ranges from -0.171 to 0.226. The interval includes no difference and permits effects in either direction. The data therefore do not provide a precise estimate of the difference between the active and sham arms.

This result does not demonstrate that the arms are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the uncertainty is sufficiently narrow to exclude differences outside that margin. Such a margin and an equivalence analysis are not reported in the registry record. A non-significant unadjusted p-value likewise cannot establish equality or rule out meaningful differences.

The primary endpoint is a safety count, not a direct measure of migraine prevention. The registry also posts a secondary mean-change comparison for headache days, but its interval includes zero and the record does not provide numerical results for the other listed secondary outcomes. These data should be described as preliminary estimates rather than as definitive evidence about clinical benefit. They do not establish the effect of treatment beyond the study period or in populations not represented by the registry’s description.

The posted serious-event summaries add descriptive safety information, but do not establish whether events were caused by a device. They also do not give a complete account of event timing, severity, or participant-level overlap. In general, event counts and comparative estimates are interpreted alongside their definitions, follow-up, and analysis methods; several of those details are not reported in the registry record.

The study’s stated aim was to assess feasibility and collect preliminary clinical data to support development of a larger pivotal study. The results are consistent with that exploratory role: they provide observed summaries and uncertain group estimates that may inform further investigation. They should not be taken as a treatment recommendation, proof of benefit, proof of no benefit, or proof of equal safety.

17. Why This Trial Matters Statistically

This trial illustrates why an estimate should be read together with its uncertainty. The primary comparison has an observed risk-difference estimate, but its confidence interval spans zero and extends in both directions. Looking only at the point estimate or the p-value would hide how much uncertainty remains about the group contrast. The interval is central to understanding what the data can and cannot distinguish.

It also shows why endpoint definition matters. A count of participants with adverse events is not the same as a count of events, an assessment of event severity, or a measure of headache frequency. The primary safety outcome and the headache-day secondary outcome represent different domains. Keeping them distinct avoids treating an outcome in one domain as confirmation of a result in another.

The pilot purpose is statistically relevant. Preliminary studies can produce estimates that help characterize uncertainty and inform planning, but their results are not automatically confirmatory. The registry’s planning illustration shows how sample-size requirements depend on the assumed effect size and target power. Those calculations are conditional examples rather than a record of the original trial’s design rationale.

Finally, the record highlights the importance of complete reporting. The registry identifies several secondary outcomes, but numerical results are not reported for all of them. It also does not report the multiplicity strategy, detailed missing-data methods, or full analysis plan. These gaps make it harder to assess how results across outcomes were selected and interpreted. Careful statistical reading separates what the registry documents from what remains unknown.

18. 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.

Several limitations specific to this trial constrain interpretation. The study is described as a pilot, and the posted arm summaries are relatively limited in size. The primary risk-difference interval is wide and includes both negative and positive values. This leaves considerable uncertainty about the direction and magnitude of the primary comparison, even though the registry provides a point estimate and an unadjusted p-value.

The registry’s outcome reporting is incomplete for the listed secondary measures. Numerical results are posted for mean change in headache days, but results for headache days by peak severity, pain-relief medication use, and SF-12 quality-of-life change are not reported in the registry record. This prevents assessment of whether findings were consistent across the outcomes named in the study record.

Important analytic details are also absent. The record does not report the original statistical analysis plan, the primary endpoint’s detailed event definition, the handling of missing outcomes, an intention-to-treat definition, adjustment for multiplicity, or any interim analysis plan. It does not explain why the secondary headache-day denominators differ from those for the primary endpoint. These omissions prevent a fuller appraisal of the analysis population and potential effects of missing data.

The sham-arm description mentions active treatment during Phase 3 after sham treatment in Phase 2, but the registry does not provide enough detail to assess how that phase relates to the randomized-period comparison. Further information about treatment adherence, event attribution, follow-up beyond the randomized period, and the generalizability of the enrolled population is not reported in the registry record. These limitations do not prove bias or invalidate the reported estimates; they define what can be assessed from the registry entry.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Non-Invasive Neurostimulation for the Prevention of Chronic Migraine — NCT01667250.
• Registry record last updated 2018-06-20; status last verified 2018-05.
• Results first posted 2018-06-20.
• 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.

22. Record Summary

The registry record describes NCT01667250, “Non-Invasive Neurostimulation for the Prevention of Chronic Migraine,” sponsored by ElectroCore INC. It is listed as a completed, randomized, double-blind, parallel, sham-controlled pilot study, with enrollment of 59. The recorded start is 2012-10 and primary completion is 2014-05; the phase is listed as NA.

The active and sham interventions were GammaCore devices. The primary outcome was the number of participants with adverse events in the randomized population during a period of up to 8 weeks. The record also lists secondary outcomes related to headache days, pain-relief medication use, and quality of life. Numerical results are posted for the primary safety outcome and mean change in headache days, while results for several other listed secondary measures are not reported in the registry record.

The study was intended to assess feasibility and gather preliminary safety and clinical data in support of a larger pivotal study. The posted comparisons have substantial uncertainty, and the registry does not report several details needed for a fuller assessment of analysis, multiplicity, and missing data.