A Study of Lasmiditan in Healthy Elderly Participants: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Lasmiditan in Healthy Elderly Participants (NCT03406260), a randomized phase 1 study. The primary outcome is Pharmacodynamics: Change From Baseline in Peak Hourly Mean Values of Systolic Blood Pressure (SBP).

2. Clinical Question

3. Trial Design

This was a phase 1 randomized, double-masked crossover study of lasmiditan and placebo in healthy elderly participants. The registry record lists an enrollment of 36 and the status as completed. The study start date was 2018-01-25, and primary completion was 2018-04-13. The brief description says the study would take about 11 days, not including screening, and that screening was required within 28 days before the study began.

The intervention descriptions include lasmiditan 200 mg, lasmiditan 100 mg, and placebo. Each regimen is described as an oral tablet in the fasted state, taken in the morning on Days 1, 3, and 5 while seated, with approximately 240 mL of room-temperature water. The crossover designation means the design compares treatments within a crossover framework, but the registry record does not report the treatment sequences, the order in which participants received regimens, or the intervals between administrations. It also does not report details of how masking was maintained.

The primary outcome was pharmacodynamic: change from baseline in peak hourly mean systolic blood pressure, with measurements through 24 hours after each administration. The registry describes continuous ambulatory monitoring and a linear mixed-effects analysis that adjusted for baseline, treatment, treatment sequence, period, treatment by time point interaction, and a random participant effect. Two secondary outcomes are listed, both pharmacokinetic: maximum concentration and area under the concentration-versus-time curve from zero to infinity. Their numerical results are not reported in the record.

The posted primary results include treatment-group estimates and sponsor-reported non-inferiority analyses. These are not identical forms of evidence: the unadjusted re-calculations compare posted summary statistics, while the sponsor analyses are the registry's reported model-based tests. The record does not report the original sample-size justification or enough detail to reconstruct every aspect of the planned statistical analysis.

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: Crossover study with three study periods, each participant received single oral doses of Lasmiditan 200 milligrams (mg), Lasmiditan 100 mg and Placebo tablets as per the dosing sequence in each period. The washout period between dosing in consecutive study periods was at least 48 hours.

Period 1

Reasons for not completing this period:

Period 2

Period 3

Analysis population for the primary outcome, as defined in the registry: All randomized participants who received at least one dose of study drug and have data for SBP

5. Baseline Characteristics

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

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

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Pharmacodynamics: Change From Baseline in Peak Hourly Mean Values of Systolic Blood Pressure (SBP), measured over Baseline through 24 hours after each administration of study drug.

The primary endpoint is change from baseline in peak hourly mean systolic blood pressure (SBP), expressed in millimeters of mercury (mmHg), through 24 hours after each administration. SBP is the upper value in a blood-pressure reading. The study used a 24-hour ambulatory blood pressure monitoring device on the participant's nondominant arm, rather than relying only on a single measurement in a clinic. The device recorded measurements every 20 minutes during daytime hours and every 30 minutes during nighttime hours. For statistical analysis, diurnal hours were defined as 0800 to 2100 and nocturnal hours as 0000 to 0600.

As a general statistical point, repeated ambulatory readings can describe the pattern of a continuous measure across time and can support estimates of hourly means. A peak hourly mean focuses on the largest hourly mean change in the specified monitoring period, rather than on one isolated reading. The registry states that least-squares means were estimated with a linear mixed-effects model that accounted for baseline and treatment-related design factors, including period and sequence, as well as a participant-level random effect. The endpoint is a blood-pressure measure; it is not itself a measure of symptoms, clinical events, or long-term outcomes.

The record's endpoint description names change from baseline, while the reported arm values are labeled least-squares means and their dispersion is standard error. The posted results do not give detailed hourly trajectories or further information about how the peak hourly value was selected. Those details limit how fully the precise endpoint construction can be independently evaluated.

7. Results Posted in the Registry

• Lasmiditan 200 mg: mean 15.79 versus 17.14 on control; difference -1.35 (95% CI -6.30 to 3.60), standardized effect d = -0.13; z-test p = 0.593.
• Lasmiditan 100 mg: mean 15.50 versus 17.14 on control; difference -1.64 (95% CI -6.65 to 3.37), standardized effect d = -0.15; z-test p = 0.521.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is continuous: it is a blood-pressure change measured on a numeric scale. For continuous outcomes, a group mean describes the central value, while a standard error describes the estimated precision of that mean. A smaller standard error generally indicates a more precisely estimated mean, but it does not describe the spread of individual participants' measurements in the same way as a standard deviation. The registry identifies the arm estimates as least-squares means and the accompanying dispersion as standard error.

What does a least-squares mean represent?

As a general statistical explanation, a least-squares mean is a model-based estimate of a group mean, adjusted for factors included in the statistical model. It is not necessarily the same as a simple average of all raw observations. The registry says that its linear mixed-effects model adjusted for baseline, treatment, treatment sequence, period, treatment by time point interaction, and a random effect of participant. This structure is relevant to a crossover trial because measurements may depend on the treatment period or sequence, and repeated observations from the same participant are related rather than independent.

A mixed-effects model can represent both fixed effects, such as treatment and period, and participant-specific variation through a random effect. As a general point, accounting for within-participant correlation can make estimates and uncertainty more appropriate for repeated measurements. The record gives the listed model terms, but it does not provide the full model specification, the covariance structure, diagnostics, or detailed handling of incomplete repeated measurements. Those parts of the analysis are not reported in the registry record.

What does the crossover structure change?

In a crossover design, participants can contribute observations under more than one treatment condition. This can enable comparisons that account for stable differences between participants. However, interpretation depends on the treatment sequence, period effects, and whether earlier exposure could affect later measurements. The registry identifies the study as crossover and says sequence and period were included in the model. It does not describe the sequences themselves, the timing between treatment periods, or any assessment of carryover. It would therefore be inappropriate to assume details of those design features beyond what the record states.

The posted arm summaries list 36 participants for lasmiditan 200 mg, 34 for lasmiditan 100 mg, and 35 for placebo. These counts differ across treatment conditions. The primary population is described as randomized participants who received at least one dose and had SBP data. The record does not explain the differing counts or report a separate flow of participants through each analysis. A crossover analysis can use observations from participants who have data for some, but not all, periods, depending on the model and analysis rules; the registry record does not specify how that situation was handled.

What is the unadjusted re-calculation?

The re-calculated comparisons use the posted summary estimates and their standard errors to make simple, unadjusted comparisons of each lasmiditan group with placebo. They yield mean differences, confidence intervals, and unadjusted p-values. These are not a reconstruction of the registry's full mixed-effects model. In particular, the posted summaries do not contain the participant-level data or all model covariance information needed to reproduce the sponsor's adjusted analysis. The re-calculated estimates are therefore useful as a separate descriptive check, not as a substitute for the sponsor's analysis.

The re-calculation also uses an approximate pooled standard deviation derived from the posted standard errors and sample counts. Since the endpoint is from a crossover study, an unadjusted comparison based on arm-level summaries does not make full use of within-participant pairing. The re-calculated results should be read with that limitation in mind. The record flags a discrepancy between these calculations and the reported results, so the sponsor's own analysis takes precedence.

How should p-values be read?

As a general explanation, a p-value describes how compatible data are with a specified statistical null hypothesis under the assumptions of the test. It is not the probability that a treatment is effective, that the null hypothesis is true, or that the result will repeat. The re-calculated p-values of 0.593 and 0.521 are explicitly unadjusted. The registry's sponsor-reported values are p < 0.001 and are associated with analyses labeled non-inferiority. Because the analysis types and hypotheses differ, the p-values should not be compared as if they were results from an identical test.

Non-inferiority analysis generally asks whether a treatment's effect is not worse than a comparator by more than a prespecified margin. That margin is essential to interpreting the result. The record's listed confidence intervals have lower bounds of -1000, but the registry information does not explain that bound or provide a usable margin for interpreting it. The reported non-inferiority label and p-values can be stated as recorded, but the underlying criterion cannot be fully assessed from these details.

Why can over-dispersion matter?

As a general statistical point, over-dispersion occurs when observed variation is greater than a model assumes. If a model understates variability, standard errors may be too small and confidence intervals too narrow; if variability is modeled appropriately, uncertainty estimates better reflect the data. The primary endpoint is continuous, and the posted summaries do not include enough information to assess over-dispersion or model fit. It is not appropriate to infer that over-dispersion was present or absent in this trial. Assessing the model would require details such as residual behavior and the variance-covariance assumptions, which are not reported in the registry record.

The registry lists two secondary pharmacokinetic outcomes: maximum concentration and area under the concentration-versus-time curve from zero to infinity. The record information does not include their numerical results or statistical analyses. Thus, no interpretation of those secondary outcomes is possible. More broadly, the number of outcome measures and analyses listed does not reveal whether multiplicity adjustments were made; the adjustment strategy is not reported in the registry record.

10. Confidence Intervals and Precision

A confidence interval gives a range of values reasonably compatible with the data and the assumptions of the analysis. It communicates precision as well as direction: a wider interval leaves more uncertainty about the size and direction of the contrast. It is not a guarantee that the true value lies in the interval, nor does it describe the range of individual participants' measurements.

For lasmiditan 200 mg versus placebo, the unadjusted re-calculated mean difference is -1.35, and the 95% confidence interval extends from -6.299 to 3.599. For lasmiditan 100 mg versus placebo, the re-calculated mean difference is -1.64, with a 95% confidence interval from -6.653 to 3.373. Each interval spans zero and includes values on both sides of it. The interval widths indicate that the re-calculated contrasts are not estimated precisely enough to distinguish a small difference from a range of larger differences in either direction.

These intervals come from unadjusted re-calculations based on posted summary statistics, not the registry's full mixed-effects analysis. The sponsor-reported 95% confidence intervals are recorded with lower bounds of -1000 and upper bounds of 1.81 for lasmiditan 100 mg, and 2.06 for lasmiditan 200 mg. Because the record does not explain the -1000 lower bounds, they do not permit a clear assessment of precision as recorded. The discrepancy between the sponsor analyses and the summary-statistic re-calculations means the sponsor's own analysis takes precedence. Neither set of intervals should be read as evidence of exact equivalence between treatments.

As a general point, precision depends on the amount of information, outcome variability, design, and analysis. The posted group counts are limited, and the record does not report the original sample-size justification. The estimates and intervals describe this study's posted results; they do not establish how precisely a different population or longer follow-up would be characterized.

11. 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 trial's original design calculations. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These figures are participants per arm for 80% power or participants per arm for 90% power; they are not total-event counts. The table and curve show how the planning estimate changes across the listed effect assumptions.

The 80% power column means the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one. The 90% power column expresses the same idea with a higher target chance of detection, which generally requires more participants. Neither column is a count of participants observed in this trial. These planning illustrations are not observed power.

The rows for planning for 75% or 50% of the observed effect use smaller effects than the row for 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm. The displayed values are specific to the corresponding lasmiditan-versus-placebo comparison and its re-calculated effect. They should not be treated as a proposed design for another study without considering its endpoint, analysis, and assumptions.

The record does not report the trial's original sample-size justification or the assumptions used when the study was designed. The illustration's assumptions are therefore separate from the actual design rationale. The calculations also use a normal approximation and equal allocation; the registry identifies the study as a crossover, so these simplified two-arm planning values should not be confused with a detailed calculation for the original crossover design.

12. 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 = -1.350; pooled standard deviation σ = 10.638.
2. n = 2 × (1.96 + 0.842)² × 10.638² / -1.350² = 974.7, rounded up to 975 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 <- -1.35                      # observed difference in means
sigma <- 10.6376923985053                     # 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(3406260)
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 = 975 (80% power), 1,305 (90% power)
 75% of observed effect: n per arm = 1,733 (80% power), 2,320 (90% power)
 50% of observed effect: n per arm = 3,899 (80% power), 5,220 (90% power)
power.t.test: 975.6 
Simulated power at n = 975 per arm: 0.799 (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.

13. Analyses Reported by the Sponsor

The registry's sponsor-reported analyses use a linear mixed-effects model and are labeled non-inferiority. For lasmiditan 100 mg versus placebo, the reported estimate is -1.63, the listed 95% confidence interval runs from -1000 to 1.81, and the reported p-value is p < 0.001. For lasmiditan 200 mg versus placebo, the reported estimate is -1.35, the listed interval runs from -1000 to 2.06, and the reported p-value is p < 0.001. These values are transcribed as recorded; the registry does not explain the lower bound of -1000.

The separate re-calculations use posted treatment-group summaries to produce unadjusted mean differences and confidence intervals. They give -1.64 for lasmiditan 100 mg versus placebo and -1.35 for lasmiditan 200 mg versus placebo, with unadjusted p-values of 0.521 and 0.593, respectively. They do not reproduce the sponsor's full model or its non-inferiority test. The two sets of results therefore should not be treated as interchangeable.

A discrepancy is flagged between the sponsor-reported analysis and the re-calculation. In that situation, the sponsor's own analysis takes precedence. The re-calculated results can still illustrate what follows from a simple comparison of the posted summary statistics, but they are not a correction to the sponsor's analysis. The registry record does not report enough detail to resolve the unusual confidence-interval bounds or fully assess the non-inferiority criterion.

14. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is change from baseline in peak hourly mean SBP. The registry also lists two secondary pharmacokinetic outcomes: maximum concentration and area under the concentration-versus-time curve from zero to infinity. The record lists three outcome measures and two analyses, but the information available does not describe a multiplicity-control strategy. It is therefore not reported in the registry record whether the analyses were adjusted for multiple outcomes, comparisons, time points, or other statistical tests.

As a general statistical point, testing multiple outcomes or contrasts can increase the chance of at least one apparently unusual result when all null hypotheses are true. Multiplicity procedures can control that risk, but the appropriate approach depends on the prespecified analysis plan and the role of each endpoint. Because the registry does not report the adjustment strategy, the unadjusted re-calculated p-values should be understood as unadjusted; no claim about family-wise error control or other adjustment can be made.

The registry describes the primary analysis population as all randomized participants who received at least one dose of study drug and had SBP data. That definition identifies the intended population for the primary outcome, but the record does not provide a full participant flow or explain the differing endpoint counts across treatment conditions. It does not report how missing measurements were handled, whether imputation was used, or whether sensitivity analyses assessed the effect of missing data.

In a crossover design, incomplete data in one period can affect which treatment observations are available for a participant. As a general point, mixed-effects models can use incomplete repeated measurements under assumptions about the missingness process, but the validity of that approach depends on the circumstances and model. The registry's model description does not establish which missing-data assumptions were made or whether they were examined. Those details are not reported in the registry record.

The registry identifies the trial as randomized and double-masked, but the information does not include a detailed protocol or statistical analysis plan. Interim analyses, prespecified multiplicity procedures, and additional analysis populations are not reported in the registry record. Their absence from the available description should not be interpreted as proof that they were or were not performed.

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 5% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures report 0 serious events for each treatment group. The numbers at risk were 36 for lasmiditan 200 mg, 35 for lasmiditan 100 mg, and 35 for placebo. The record also lists 0 deaths in each group. These are counts from the posted safety information, not estimates of comparative risk.

A zero count in a small study does not establish that an event cannot occur or that groups have identical safety profiles. It means no serious adverse events were recorded in the listed groups in this trial's posted results. The study enrolled healthy elderly participants and the registry describes a short study period of about 11 days, not including screening. The safety counts therefore refer to this study and its reported observation period; they do not characterize longer-term or broader-population safety.

The record also lists other adverse events affecting 15 participants in the lasmiditan 200 mg group, 6 in the lasmiditan 100 mg group, and 0 in the placebo group. These are separate from the serious-event figures. The registry information does not list event terms for the serious-event category. The counts should be read descriptively, without inferring causation or making a treatment recommendation.

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

The posted primary endpoint concerns change in peak hourly mean systolic blood pressure after study-drug administration in healthy elderly participants. The registry reports model-based least-squares mean values for each treatment condition and sponsor-reported non-inferiority analyses. Separate, unadjusted re-calculations from the posted summaries produce mean differences of -1.35 for lasmiditan 200 mg versus placebo and -1.64 for lasmiditan 100 mg versus placebo. Their confidence intervals include zero and span a range of values in both directions.

These results do not establish that the treatments have exactly the same effect. A confidence interval that includes zero can be compatible with no difference, but it can also include nonzero differences. Conversely, a non-inferiority label and a small p-value cannot be fully evaluated without a clear margin and interpretable interval. The sponsor's recorded lower confidence bounds are -1000, which the registry record does not explain. Since a discrepancy is flagged, the sponsor's own analysis takes precedence over the simple re-calculation, while the available details leave important aspects of its non-inferiority interpretation unresolved.

The primary endpoint is a physiological measurement over a limited period after dosing. It is not a direct assessment of symptoms, clinical events, quality of life, or longer-term outcomes. The trial's population is healthy elderly participants, so the result should not be assumed to apply to people with a medical condition or to other populations. The record lists pharmacokinetic secondary outcomes, but their numerical results are not reported in the information.

As a general statistical principle, a study result is most useful when its estimate, uncertainty, endpoint definition, analysis population, and analysis assumptions are considered together. Here, the record supports a description of the reported blood-pressure estimates and the distinction between sponsor analysis and unadjusted re-calculation. It does not support medical advice or a broad claim about clinical benefit or harm. It also does not permit a full independent assessment of the sponsor's non-inferiority conclusion because the lower confidence bounds and the relevant margin are not explained.

17. Why This Trial Matters Statistically

This trial raises several useful statistical issues in a compact setting. It uses a crossover design and repeated ambulatory blood-pressure measurements, so the comparison involves both treatment conditions and time-dependent measurements. The registry's mixed-effects model accounts for baseline, treatment, sequence, period, treatment by time point interaction, and participant-level variation. This illustrates why an analysis of repeated measurements may need to account for both design structure and correlation within participants.

The record also shows why a model-based sponsor analysis should not be conflated with a simple re-calculation from group summaries. The re-calculated mean differences and confidence intervals are based on posted summary statistics and do not reproduce the full crossover model. They offer a separate view of the estimates but do not replace the sponsor's analysis. The discrepancy flag makes that distinction especially important: the sponsor's own analysis takes precedence, while the reported lower interval bounds still require clarification for full interpretation.

Another statistical lesson is that the purpose of a test matters. A non-inferiority analysis and an unadjusted comparison with a conventional null of no difference address different questions. A small p-value attached to a non-inferiority analysis should not be read as the same evidence as a small p-value from a test of equality. The margin and interval are essential to understanding what the non-inferiority result means, and the registry record does not explain the listed -1000 bound.

Finally, sample-size planning illustrations are not observed power and are not a record of the study's original design justification. They show how planning requirements depend on the effect size assumed, under stated simplifying assumptions. Keeping design-stage planning, observed estimates, and sponsor-reported inferential results separate helps prevent overinterpretation of any one statistic.

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.

The registry record does not report the detailed treatment sequences, timing between crossover periods, or any evaluation of carryover. Although sequence and period are listed as model terms, the available description does not permit a full assessment of those design features. The record also does not give the full model specification, covariance assumptions, diagnostic results, or detailed handling of incomplete repeated measurements.

The posted arm counts for the primary endpoint differ across conditions, and the record does not explain the differences. It identifies the primary population as randomized participants who received at least one dose and had SBP data, but does not provide a complete flow of participants into each analysis. Missing-data methods and sensitivity analyses are not reported in the registry record.

The sponsor-reported non-inferiority intervals have lower bounds of -1000, and the record does not explain that value. The non-inferiority margin is also not described in the information. These omissions make it difficult to evaluate the sponsor's reported non-inferiority findings, even though the discrepancy flag means its analysis takes precedence over the unadjusted re-calculation.

The re-calculated estimates are based on summary statistics, use an approximate pooled standard deviation, and do not account for all features of a crossover analysis. They should be viewed as simple unadjusted comparisons rather than a reproduction of the sponsor model. The registry does not report the original sample-size justification, multiplicity procedures, or interim-analysis details. Numerical results for the listed pharmacokinetic secondary outcomes are not reported. Finally, the study concerns a short monitoring period in healthy elderly participants, which limits the scope of what its primary endpoint can describe.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of Lasmiditan in Healthy Elderly Participants — NCT03406260.
• Registry record last updated 2019-12-02; status last verified 2018-05.
• Results first posted 2019-12-02.
• 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 a completed phase 1 randomized, double-masked crossover study of lasmiditan and placebo in healthy elderly participants, with enrollment of 36. The primary endpoint was change from baseline in peak hourly mean SBP through 24 hours after each administration, measured by ambulatory monitoring. The regimens included lasmiditan 200 mg, lasmiditan 100 mg, and placebo.

The posted results include treatment-group least-squares means and standard errors, sponsor-reported non-inferiority analyses, and unadjusted re-calculations from summary statistics. The re-calculated intervals include zero; the sponsor analysis is distinct and its recorded confidence intervals include lower bounds of -1000 that are not explained. Because a discrepancy is flagged, the sponsor's own analysis takes precedence. The registry also lists two pharmacokinetic outcomes, but their numerical results are not reported in the information. Serious adverse event counts and deaths are reported as 0 in each group.