A Multicenter Assessment of LBR-101 in High Frequency Episodic Migraine: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Multicenter Assessment of LBR-101 in High Frequency Episodic Migraine (NCT02025556), a randomized phase 2 study. The primary outcome is Mean Change From Baseline in the Monthly Migraine Days During the 28-day Post Treatment Period Ending With Week 12.

2. Clinical Question

3. Trial Design

This was a phase 2, randomized, double-blind, placebo-controlled, parallel-group study. The official title describes the trial as quadruple-masked; the registry lists masking as quadruple. It was multicenter, and the listed sponsor was Teva Branded Pharmaceutical Products R&D, Inc. The record reports enrollment of 297 participants, a start date of 2014-01-31, primary completion on 2015-01-31, and completed status.

Participants were assigned to high-dose LBR-101, low-dose LBR-101, or placebo. Each regimen was administered subcutaneously monthly for 3 administrations. The posted primary endpoint results include 104 participants in the placebo group, 95 in the low-dose group, and 96 in the high-dose group. These are the reported endpoint counts; they should not be treated as a new account of the allocation process.

The primary outcome covered baseline through week 12 and was the mean change in monthly migraine days during the 28-day post-treatment period ending at week 12. The defined analysis population included randomized participants who received at least one dose and obtained at least one endpoint measurement. The registry does not report the randomization ratio, the original sample-size justification, or detailed procedures for allocation concealment.

The study also posted a secondary outcome concerning change in days with headache of any severity. The registry includes one posted secondary outcome result. The available record does not establish whether that outcome or other outcomes were prespecified in a complete protocol, or how the reported outcome set relates to all measures collected during the trial.

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: Participants were assigned to receive either subcutaneous administration of 675 mg of fremanezumab (LBR-101) for three months, subcutaneous administration of 225 mg of fremanezumab (LBR-101) for three months, or subcutaneous administration of placebo for three months.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population includes all randomized participants that received at least one dose and obtained at least one endpoint measurement.

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.

6. Primary Endpoint

The registry lists the primary outcome as Mean Change From Baseline in the Monthly Migraine Days During the 28-day Post Treatment Period Ending With Week 12, measured over Baseline to week 12.

The primary endpoint was mean change from baseline in monthly migraine days during the 28-day post-treatment period ending at week 12. It was measured in days. The registry defines a migraine day using several possible situations: a day with at least 4 consecutive hours of headache meeting migraine criteria; a day meeting probable migraine criteria; use of triptans or ergot compounds to treat a headache of any duration; or certain days immediately before or after a headache day. Participants rated headache severity daily as no pain, mild, moderate, or severe.

A change score expresses how the endpoint during follow-up differs from its baseline value. In the posted results, negative mean changes indicate fewer migraine days than at baseline. A comparison of mean changes between a treatment group and placebo asks whether the average change differed between those groups, not whether every participant changed in the same way.

This endpoint was used to quantify migraine-day frequency over a specified period, rather than relying only on a general impression of improvement. The 28-day window provides a defined observation period for counting days, while the endpoint’s operational definition determines which headache and medication-use days qualify. The registry record does not report additional details about how baseline monthly migraine days were established or how incomplete daily records were handled.

7. Results Posted in the Registry

• Low Dose: mean -6.27 versus -3.46 on control; difference -2.81 (95% CI -4.31 to -1.31), standardized effect d = -0.52; z-test p = <0.001.
• High Dose: mean -6.09 versus -3.46 on control; difference -2.63 (95% CI -4.10 to -1.16), standardized effect d = -0.50; z-test p = <0.001.

8. Secondary Efficacy Endpoints

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

Change From Baseline in Number of Days With Headache of Any Severity

• 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:
  • Low Dose: mean -6.14 versus -3.52 on control; difference -2.62 (95% CI -4.13 to -1.11), standardized effect d = -0.48; z-test p = <0.001.
  • High Dose: mean -6.10 versus -3.52 on control; difference -2.58 (95% CI -4.06 to -1.10), standardized effect d = -0.48; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Low Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for High Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts one secondary outcome: change from baseline in days with headache of any severity through week 12. The overall pattern is similar to the primary outcome in that mean changes are negative in placebo and both LBR-101 groups, and the recalculated comparisons favor larger reductions in the LBR-101 groups than in placebo. This broad pattern is directionally consistent with the primary endpoint, which counts migraine days using its more specific definition.

The secondary measure is not interchangeable with the primary endpoint. It counts days with headache of any severity, whereas the primary outcome uses defined migraine-day criteria that include headache features, acute medication use, and specified adjacent headache days. Agreement in the broad direction can provide context, but it does not make the endpoints equivalent or show that they measure precisely the same experience.

The secondary comparisons are recalculated from posted summary statistics and are unadjusted. The registry does not post sponsor-reported analyses for this secondary outcome. Since multiple outcomes and comparisons may be examined, unadjusted secondary p-values do not account for the chance of finding apparently notable results across repeated testing. They also do not establish that the secondary endpoint was a confirmatory test or that its analysis was prespecified. Such details are not reported in the registry record.

For those reasons, secondary results are best treated as supportive context rather than as a second independent confirmation of the primary finding. They can indicate whether another related measure has a broadly similar pattern, while retaining the distinctions in endpoint definition, analysis method, and evidential weight. The registry’s limited reporting does not allow a complete assessment of the planned hierarchy of outcomes or the role assigned to this secondary measure.

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

• Change From Baseline in Number of Days With Headache of Any Severity

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary analysis is described as a mixed models analysis of mean differences in final values. The registry gives estimates, 95% confidence intervals, and p-values for the low-dose and high-dose groups, each compared with placebo. A mixed model can account for structured relationships among repeated observations or other modeled sources of variation, but the registry record does not report the model formula, covariance structure, adjustment variables, or the detailed treatment of incomplete measurements. Those specifics should not be inferred from the method label alone.

What does a mean change describe?

A mean is the arithmetic average of observed values. Here, the endpoint is a continuous measure expressed in days, and the posted arm values are least-squares means for change from baseline. A negative value means that the average endpoint value was lower than baseline. The comparison estimate is the difference between treatment and placebo mean changes as analyzed. Because both groups can change over time, the treatment-versus-placebo estimate is not the same as the treatment group’s change alone.

Least-squares means are model-based averages rather than necessarily simple arithmetic averages. They can reflect the model used to estimate group results. The registry identifies the parameter as a least-squares mean for the arm results and describes the sponsor’s comparison analysis as a mixed models analysis. It does not give enough detail to reconstruct the sponsor’s estimates or determine which covariates or repeated-measure structure were used.

What does the standard error tell the reader?

The arm-level results report standard errors. A standard error describes the estimated uncertainty in a mean, not the spread of individual participant outcomes. A smaller standard error generally indicates a more precise estimate of the mean, given the analysis and data. It should not be interpreted as a range containing most participants’ values. The posted arm-level standard errors are not themselves confidence intervals.

The recalculated comparisons use a simple unadjusted approach based on posted arm summaries. The pooled standard deviations used for those recalculations are approximate because the arm results report standard errors rather than individual-level outcome variability. This makes the recalculated results useful as a transparent check on the order and scale of the comparisons, but not a replacement for the sponsor’s model-based analysis.

How should the p-values be read?

A p-value evaluates how compatible the observed data are with a specified null hypothesis under the statistical model. For these comparisons, the null concerns no mean difference between an LBR-101 group and placebo. The registry reports p < .0001 for both sponsor analyses; the simple recalculations report p < 0.001 for both comparisons. These statements do not give the probability that the null hypothesis is true, and they do not measure the probability that the result will repeat in another study.

The recalculated p-values are unadjusted. They do not account for testing multiple dose comparisons or multiple outcomes. The registry record does not report whether or how the sponsor adjusted the primary analyses for multiplicity. Thus, the reported p-values should be read in the context of the analysis plan, which is not fully described in the record.

Why can the reported and recalculated estimates differ?

The sponsor’s mixed models analysis and the simple recalculation do not necessarily use the same statistical model or information. The sponsor’s reported low-dose estimate is -2.81, while its high-dose estimate is -2.64. The unadjusted recalculation gives -2.81 and -2.63, respectively. The small differences in the high-dose estimate and the confidence limits are consistent with using different analysis approaches and rounding. The recalculation also uses approximate variability derived from standard errors. The registry record does not report enough model detail to reproduce the sponsor’s analysis exactly.

When a sponsor analysis and a simplified recalculation differ, they answer closely related but not necessarily identical statistical questions. The sponsor’s analysis is the trial’s reported analysis; the recalculation is an independent, unadjusted comparison using summary statistics. The record flags no discrepancy, and the numerical results are close. Neither the closeness nor the small differences remove the need to consider the model specification, missing data, and multiplicity information that is not reported.

What is the role of the endpoint definition?

Statistical analysis depends on how an outcome is defined before values are analyzed. The registry’s migraine-day definition includes qualifying migraine or probable migraine headache, use of specified acute medicines for headache, and certain headache days adjacent to qualifying days. A different definition could count a different set of days, so interpretation should remain tied to the stated definition. The record gives the operational criteria but does not provide a full account of endpoint adjudication or data-cleaning rules.

Overall, the methods support a comparison of group-average change, with uncertainty represented by confidence intervals and p-values. The registry gives the broad analysis label and principal outputs, but not all implementation details needed for a full statistical audit. The recalculation is consequently best used as a check on the reported comparison, not as a substitute for the trial’s own analysis.

11. Confidence Intervals and Precision

The sponsor-reported 95% confidence interval for the low-dose comparison extends from -4.07 to -1.55 days. For the high-dose comparison, it extends from -3.9 to -1.38 days. Both intervals are entirely below zero, which is consistent with the reported negative mean differences. Their endpoints also show that the estimates are not exact: the data are compatible with a range of mean differences under the model used.

A confidence interval is a measure of statistical precision, not a guarantee that the true effect lies in the specific interval for this one study. In repeated use of the same procedure under its assumptions, such intervals have a stated coverage property. The width reflects both the amount of information and the variability represented by the analysis. It does not show how much individual participants’ responses varied; that requires different summaries.

The recalculated intervals are -4.307 to -1.313 for low dose and -4.099 to -1.161 for high dose. They are based on an approximate standard deviation and a simple unadjusted comparison, whereas the sponsor’s intervals come from mixed models. Differences between these intervals should therefore be read as consequences of distinct approaches, not as evidence that one set can be substituted for the other. The registry record does not report the model details needed to independently reproduce the sponsor’s interval estimates.

Precision also depends on the endpoint and follow-up window. These intervals concern mean change in monthly migraine days in the 28-day period ending at week 12, not a different outcome or a longer-term effect. Their statistical precision does not resolve uncertainties about missing measurements, multiplicity, generalizability, or the stability of results in other populations.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for the listed two-group comparisons. They are not total event counts: this is a continuous endpoint, and the planning illustration expresses sample size as participants in each arm. Each comparison is planned separately against placebo, rather than as a single three-arm total. The registry’s original trial sample-size assumptions and justification are not reported in the registry record.

The illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed comparison effect as its starting point, then considers detecting 100%, 75%, or 50% of that observed effect. The figures under 80% power describe the participants per arm calculated to give an 80% chance of detecting the specified effect under those assumptions if that effect is present. The 90% power figures use a higher probability of detecting the same specified effect, and therefore require more participants per arm.

For example, planning for 75% of the observed low-dose effect gives 103 participants per arm for 80% power and 138 participants per arm for 90% power. For the high-dose comparison, the corresponding figures are 114 and 152 participants per arm. Planning for 50% of the observed effect requires larger samples than planning for the full observed effect. This reflects a general principle: smaller effects are harder to distinguish from random variation and need more participants for the same power target.

These calculations are planning illustrations based on the observed results, not evidence about the design process that produced this trial’s enrollment. They are not observed power. Their estimates depend on the stated assumptions, including the observed effect used as the reference, and should not be read as a guarantee that a future study will achieve the indicated power.

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 = -2.810; pooled standard deviation σ = 5.384.
2. n = 2 × (1.96 + 0.842)² × 5.384² / -2.810² = 57.6, rounded up to 58 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 <- -2.81                      # observed difference in means
sigma <- 5.38390428784824                     # 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(2025556)
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 = 58 (80% power), 78 (90% power)
 75% of observed effect: n per arm = 103 (80% power), 138 (90% power)
 50% of observed effect: n per arm = 231 (80% power), 309 (90% power)
power.t.test: 58.6 
Simulated power at n = 58 per arm: 0.795 (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 registry reports the sponsor’s primary comparisons as mixed models analyses. The low-dose versus placebo mean difference is -2.81, with a 95% confidence interval from -4.07 to -1.55 and p < .0001. The high-dose versus placebo mean difference is -2.64, with a 95% confidence interval from -3.9 to -1.38 and p < .0001.

The simple recalculations give -2.81 for low dose and -2.63 for high dose, with unadjusted p < 0.001 for each. Their intervals are -4.307 to -1.313 and -4.099 to -1.161, respectively. The estimates are close, but the recalculated intervals differ because the recalculation uses an unadjusted summary-statistic method and approximate variability, rather than the reported mixed models analysis.

The sponsor results are the analyses reported by the trial. The recalculated figures are a secondary check, not a replacement or correction. The registry does not provide the model details required to recreate the sponsor’s output fully, and the record flags no discrepancy between the sources. Interpretation should therefore keep the two approaches distinct and give the reported mixed models analysis its role as the trial’s stated analysis.

15. Multiplicity, Missing Data and Analysis Populations

The record reports two primary treatment-versus-placebo analyses and one posted secondary outcome, but does not report a multiplicity adjustment for the primary comparisons or secondary testing. When researchers evaluate more than one comparison or outcome, the chance of at least one apparently unusual result can increase. Statistical procedures can address that issue, but the registry record does not say whether such procedures were planned or applied. The recalculated p-values are explicitly unadjusted and should not be interpreted as multiplicity-adjusted evidence.

The sponsor’s reported primary p-values come from mixed models analyses. The record does not describe any hierarchy between dose comparisons, whether one comparison was designated as primary within the primary endpoint, or how the two dose comparisons were handled statistically. It also does not provide the full protocol or statistical analysis plan. Therefore, the nominal p-values can be quoted as reported, but the record does not support a conclusion about family-wise error control or the confirmatory status of each comparison.

The registry defines the primary analysis population as randomized participants who received at least one dose and obtained at least one endpoint measurement. This is the stated operational population, but it is not identical to simply including every randomized participant regardless of treatment or measurement availability. The record does not report how many randomized participants were excluded from this population, why any were excluded, or the amount and pattern of missing endpoint data.

Mixed models can use available repeated observations under particular assumptions about missingness and model structure, but the method label alone does not establish which missing-data assumptions were used or whether they were appropriate. The registry does not report imputation methods, sensitivity analyses, or a comparison of included and excluded participants. Those omissions limit assessment of robustness if outcome availability was related to participant characteristics or treatment experience.

The registry also does not report interim analyses, stopping rules, or the original sample-size justification. This absence should not be filled by assuming that such procedures were or were not used. It limits the ability to evaluate how the reported statistical testing related to the trial’s complete prespecified plan.

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: antiphospholipid syndrome (1.0%), fibula fracture (1.0%), migraine (1.0%), tremor (1.0%), hypertensive crisis (1.0%).

The registry lists serious adverse events among 104 participants at risk in the placebo group, 96 in the low-dose group, and 96 in the high-dose group. It reports 0 participants with a serious adverse event in placebo, 2 in the low-dose group, and 2 in the high-dose group. The registry reports 0 deaths in each group. These are participant counts from the posted safety summary; they do not by themselves identify the cause of an event or establish whether an event was related to treatment.

The record lists Antiphospholipid syndrome, Fibula fracture, Migraine, Tremor, and Hypertensive crisis among the top serious-event terms, each at 1.0%. The listed terms are not sufficient to determine the clinical circumstances or treatment relationship for each event. The registry does not provide detailed narratives or a fuller account of event timing in this summary.

Serious adverse-event counts are distinct from counts of other adverse events. The record also reports other adverse events affecting 9 participants in placebo, 9 in low dose, and 11 in high dose. Those counts should not be combined with the serious-event counts. Safety summaries describe observed events over the trial period and do not, on their own, establish comparative risk or support conclusions about safety beyond the recorded follow-up and definitions.

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

The posted data show decreases from baseline in mean monthly migraine days in placebo and both LBR-101 groups during the endpoint period. The reported mixed models comparisons show larger mean reductions in each LBR-101 group than in placebo, and the associated 95% confidence intervals are entirely below zero. The simple recalculations are close to the sponsor’s estimates and point in the same direction, while relying on a less detailed, unadjusted method.

These group-level results do not mean that every participant had fewer migraine days, nor do they describe the range of individual outcomes. The registry does not report individual response distributions in the information. Mean changes can conceal differences among participants, including participants whose outcomes changed in different directions or by different amounts.

The results also do not establish a difference between the low and high doses. Each dose was compared with placebo; no direct dose-versus-dose analysis is posted. Nor do the reported results establish what would happen outside the studied population, with a different regimen, over a longer follow-up period, or under a different endpoint definition.

A small p-value is not a measure of clinical importance, and a confidence interval does not address every source of uncertainty. Interpretation remains limited by incomplete registry detail about the statistical model, missing data, multiplicity, the original design assumptions, and participant characteristics. The trial record reports a phase 2 study with an endpoint ending at week 12; it does not report long-term outcomes in this summary.

Accordingly, the appropriate reading is narrow: the registry reports statistically clear group-average differences in the specified endpoint under its stated analysis, over the stated period. That is not the same as a complete account of individual benefit, long-term outcomes, dose differences, or all aspects of the trial’s prespecified analysis plan.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through its endpoint definition, comparison, and analysis population. The outcome is not simply a broad count of headache reports: the registry defines migraine days through headache duration and criteria, medication use, and specified adjacent days. Interpretation depends on that operational definition and the particular 28-day period ending at week 12.

It also shows the value of separating within-group change from between-group comparison. All three groups had negative mean changes from baseline, but the treatment question is addressed by comparing each LBR-101 group with placebo. Without that distinction, improvement over time in the treatment groups could be incorrectly attributed entirely to the intervention rather than interpreted in the context of the control group.

The reported sponsor analysis and the recalculation offer another useful statistical distinction. A simple unadjusted comparison can check whether summary statistics yield an estimate in the same general range, but it does not reproduce a mixed models analysis. The two should be reported as different analytic approaches, with the sponsor’s analysis identified as the trial’s stated analysis and the recalculation presented as a limited check.

Finally, the record illustrates how precision and statistical significance are related but not interchangeable. Confidence intervals communicate uncertainty about the estimated comparison, while p-values address compatibility with a null model. Neither replaces information about missing data, multiplicity, the full analysis plan, or the scope of the population and follow-up. Those distinctions matter when moving from a posted result to a careful statistical 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.

Several trial-specific limitations follow from the scope and detail of the registry record. The study is phase 2, and the primary endpoint concerns a 28-day period ending at week 12. The record does not provide longer-term results in this summary, so the posted estimates address only the stated endpoint period. The results also concern the registry-defined population and should not be assumed to apply to populations or settings not described in the record.

The registry reports the overall enrollment and endpoint group counts, but the information does not describe baseline participant characteristics or the distribution of outcome values. The arm-level means and standard errors therefore cannot show how representative the participants were or how variable individual changes were. The record also does not report the actual doses, despite identifying high-dose and low-dose regimens.

Although the sponsor analysis is labeled as mixed models, the model specification, covariates, covariance structure, and missing-data procedures are not reported. The original sample-size justification, randomization ratio, allocation concealment details, multiplicity plan, and interim analysis information are also not reported in the registry record. These omissions restrict independent assessment of the planned analysis and its assumptions.

The safety summary provides group counts and selected serious-event terms, but not detailed event narratives or treatment-relatedness assessments in this summary. The posted count information should not be treated as a complete safety profile. Likewise, the registry’s single posted secondary outcome does not establish the full set of outcomes measured or the planned testing hierarchy.

These limitations concern what can be inferred from the registry record; they do not establish that omitted procedures were absent from the study. A complete protocol, statistical analysis plan, and fuller results would be needed to assess the design and analyses in greater depth.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Multicenter Assessment of LBR-101 in High Frequency Episodic Migraine — NCT02025556.
• Registry record last updated 2022-01-24; status last verified 2022-01.
• Results first posted 2022-01-24.
• 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

NCT02025556 is a completed phase 2 randomized, quadruple-masked, parallel-group study comparing monthly subcutaneous high-dose LBR-101 and low-dose LBR-101 with placebo in high frequency episodic migraine. The registry reports enrollment of 297 participants and a primary endpoint of mean change in monthly migraine days during the 28-day period ending at week 12.

The posted mixed models analyses report mean differences versus placebo of -2.81 for low dose and -2.64 for high dose, with 95% confidence intervals below zero and p < .0001 for both comparisons. The recalculated summary-statistic estimates are close, but use an unadjusted method with approximate variability. The registry also posts a secondary headache-day outcome and safety counts. Details of the original sample-size justification, full statistical plan, multiplicity handling, and missing-data procedures are not reported in the registry record.