Efficacy, Tolerability, and Safety of DFN-15: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy, Tolerability, and Safety of DFN-15 (NCT03009019), a randomized phase 3 study. The primary outcome is Percentage of Subjects Who Are Pain-free at 2 Hours Postdose (First Treated Double-blind Treatment Period).

2. Clinical Question

The primary question concerns a specific treatment occasion and a specific time point. It is not a comparison of average pain over a longer period, nor does it address every migraine symptom. The registry also lists outcomes concerning pain relief, associated symptoms, functional disability, recurrence, and adverse events. Those outcomes give a broader view of what was assessed, but they do not change the definition of the primary question.

The posted primary results are reported using two analysis approaches, labelled LOCF and OC. The sponsor’s analyses compare active treatment with placebo within each of those approaches. The registry record does not report a detailed explanation of the analysis populations behind these labels beyond identifying the primary population as Full Analysis Set 1.

3. Trial Design

This was a phase 3, randomized, triple-masked, parallel-group study of DFN-15 and placebo. The registry describes it as multicenter and reports that it was conducted in the United States. The condition listed is migraine headache, and the study focus was episodic migraine with or without aura.

Enrollment was 631. The registry lists the study start as 2016-12 and primary completion as 2017-11, with status completed. These dates describe the registry record; they do not provide the full schedule of recruitment, follow-up, or analysis.

The primary efficacy outcome was the percentage of participants pain-free 2 hours after dosing during the first treated double-blind treatment period. The analysis population is identified as Full Analysis Set 1. Results are presented for placebo and DFN-15 under LOCF and observed-case labels. In addition to the first treated period, the registry lists outcomes assessed in DB1 and DB2, including headache pain relief and freedom, symptoms, functional disability, and treatment-emergent adverse events.

Randomization and masking are features of the reported design, but details such as the randomization procedure, allocation concealment, who was masked, and how masking was maintained are not reported in the registry record. The protocol’s intended allocation ratio and the original sample-size assumptions are also not reported in the registry record. The planning illustrations associated with the posted results are separate calculations based on observed effects and should not be mistaken for the trial’s original design assumptions.

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.

Double-blind Period 1 (DB1)

Double-blind Period 2 (DB2)

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set 1

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: Safety Set 1 (for DB1)

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Subjects Who Are Pain-free at 2 Hours Postdose (First Treated Double-blind Treatment Period), measured over 2 hours postdose.

The primary endpoint is the percentage of participants who were pain-free 2 hours after taking the study drug in the first treated double-blind treatment period. The registry defines pain-free status as a change from moderate or severe pain before dosing to no pain at the postdose assessment. It identifies Full Analysis Set 1 as the population for this outcome.

This is a binary outcome: each participant either meets the stated pain-free definition at the specified assessment or does not. Reporting a percentage makes the result interpretable as the proportion meeting that endpoint in each group. Comparing the groups addresses whether their observed proportions differ at that time point.

A fixed postdose assessment offers a clearly defined snapshot of pain status. It does not, by itself, describe how quickly pain changed, whether relief was sustained, whether other migraine symptoms were absent, or how participants functioned. The registry lists separate outcomes for several of those questions. The primary endpoint is therefore one focused measure of the first treated attack, rather than a complete account of symptom experience or outcomes over the entire study.

The registry record does not report the rationale for selecting this endpoint, the planned treatment-effect threshold, or the original sample-size calculation. Those details should not be inferred from the observed outcome or the retrospective planning illustrations.

7. Results Posted in the Registry

• DFN-15 Active (LOCF): 32.9% (92/280) versus 25.8% (69/267) on control; risk difference 7.0 percentage points (95% CI -0.6 to 14.6), risk ratio 1.27 (0.98–1.65); unadjusted two-proportion z-test p = 0.072.
• DFN-15 Placebo (OC): 24.6% (63/256) versus 25.8% (69/267) on control; risk difference -1.2 percentage points (95% CI -8.7 to 6.2), risk ratio 0.95 (0.71–1.28); unadjusted two-proportion z-test p = 0.745.
• DFN-15 Active (OC): 32.4% (89/275) versus 25.8% (69/267) on control; risk difference 6.5 percentage points (95% CI -1.1 to 14.1), risk ratio 1.25 (0.96–1.63); unadjusted two-proportion z-test p = 0.095.

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.

The Number of Subjects With TEAEs After Study Drug Compared Between DFN-15 and Placebo

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • DFN-15 DB1: 10.7% (31/289) versus 9.9% (28/283) on control; risk difference 0.8 percentage points (95% CI -4.2 to 5.8), risk ratio 1.08 (0.67–1.76); unadjusted two-proportion z-test p = 0.743.
  • Placebo DB2: 10.2% (26/254) versus 9.9% (28/283) on control; risk difference 0.3 percentage points (95% CI -4.8 to 5.4), risk ratio 1.03 (0.62–1.72); unadjusted two-proportion z-test p = 0.895.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DFN-15 DB1 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Placebo DB2 and the control. The interval gives the range of effects that remain compatible with the data.

Headache Pain Recurrence Postdose (DB1 and DB2)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • DFN-15 DB1: 7.7% (22/287) versus 10.0% (28/280) on control; risk difference -2.3 percentage points (95% CI -7.0 to 2.3), risk ratio 0.77 (0.45–1.31); unadjusted two-proportion z-test p = 0.327.
  • Placebo DB2: 6.7% (17/253) versus 10.0% (28/280) on control; risk difference -3.3 percentage points (95% CI -8.0 to 1.4), risk ratio 0.67 (0.38–1.20); unadjusted two-proportion z-test p = 0.174.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DFN-15 DB1 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Placebo DB2 and the control. The interval gives the range of effects that remain compatible with the data.

Sustained Headache Pain Relief Postdose (DB1 and DB2)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • DFN-15 DB1: 55.1% (158/287) versus 39.6% (111/280) on control; risk difference 15.4 percentage points (95% CI 7.3 to 23.5), risk ratio 1.39 (1.16–1.66); unadjusted two-proportion z-test p = <0.001.
  • Placebo DB2: 44.3% (112/253) versus 39.6% (111/280) on control; risk difference 4.6 percentage points (95% CI -3.8 to 13.0), risk ratio 1.12 (0.91–1.36); unadjusted two-proportion z-test p = 0.280.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for DFN-15 DB1 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Placebo DB2 and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary questions, including treatment-emergent adverse events, associated migraine symptoms, time to relief or pain freedom, recurrence, and functional disability. The posted secondary results include measures from DB1 and DB2. Taken together, these outcomes offer additional descriptions of symptom response and tolerability, rather than a second version of the primary endpoint.

The pattern is not uniform across outcomes. Some observed secondary comparisons show a higher proportion with a favorable outcome in the DFN-15 group, while others are close between groups or have estimates with substantial uncertainty. This variation means that secondary findings should be read outcome by outcome and in relation to their definitions, assessment times, and denominators. They do not establish a single overall effect across all migraine symptoms or treatment periods.

The primary outcome asks about pain freedom at a fixed time after the first treated attack. Secondary measures such as sustained relief, recurrence, symptom absence, and adverse events address distinct questions. A favorable direction on one measure does not imply the same result on another, and secondary findings cannot replace the primary analysis.

Unadjusted secondary results carry less confirmatory weight because multiple outcomes and time points are considered. In general, testing many outcomes without a reported multiplicity strategy increases the opportunity for chance findings. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting the secondary endpoints. These results are therefore best viewed as supplementary evidence that may help frame further questions, not as independent confirmation of the primary finding.

The registry reports 16 posted secondary outcomes, while the listed outcomes include more possible measures than are fully detailed in the information available for this analysis. Outcomes without posted results or an analysis plan cannot be interpreted as either favorable or unfavorable.

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

• The Number of Subjects With TEAEs After Study Drug Compared Between DFN-15 and Placebo
• Freedom From Nausea, Photophobia, and Phonophobia Postdose (DB1 and DB2)
• Time to Headache Pain Relief Postdose (DB1 and DB2)
• Time to Headache Pain Freedom Postdose (DB1 and DB2)
• Headache Pain Relief Postdose (DB1 and DB2)
• Headache Pain Freedom Postdose (DB1 and DB2)
• Absence of Screening MBS at Time Points Postdose (DB1 and DB2)
• Change in Functional Disability Score Postdose (DB1 and DB2)

9. Statistical Interpretation

10. Statistical Methods Explained

What kind of outcome is this?

The endpoint is a binary outcome summarized as a percentage: participants either met the pain-free definition at 2 hours postdose or did not. For this type of outcome, a group percentage describes the observed frequency of the event. The percentages are accompanied by confidence intervals, which communicate uncertainty around the estimated proportions.

A comparison can be expressed on different scales. A risk difference describes the difference between proportions in the two groups, while a risk ratio compares those proportions as a ratio. An odds ratio compares the odds of the event between groups. These measures answer related but not identical questions, so their numerical values are not interchangeable. The sponsor’s reported primary analyses use odds ratios; the recalculations also present risk differences, risk ratios, and odds ratios.

What does a confidence interval communicate?

In general, a confidence interval is a range of values compatible with the observed data under the assumptions of the method. It conveys precision as well as direction: a wider interval indicates greater uncertainty than a narrower one. A 95% confidence interval is not a guarantee that the true effect lies within the specific interval, and it does not measure the probability that a treatment effect is real.

For a risk difference, a confidence interval that includes zero is compatible with no difference under that scale. For a ratio measure, the corresponding no-difference value is 1.00. The primary sponsor intervals include or touch the no-difference value, which is consistent with the reported p-values being above 0.05. This is not proof of equivalence; equivalence requires a prespecified margin and an analysis designed to assess it, neither of which is reported in the registry record.

How should p-values be read?

In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. A p-value near a conventional threshold should not be treated as categorically different from one just on the other side. Estimates and confidence intervals provide important context.

The registry reports Fisher Exact analyses for the sponsor’s primary comparisons. Fisher’s exact test is a method for comparing categorical outcomes. The reported quantities are odds ratios with confidence intervals and p-values. The recalculated unadjusted results use a separate simple comparison of the posted summary counts. Since the registry marks a discrepancy, the sponsor’s analysis is the authoritative reported analysis; the recalculation is a supplementary check, not a replacement.

Why can analysis labels matter?

The primary results distinguish LOCF from observed-case analyses. LOCF means last observation carried forward: in general, an earlier recorded value is carried forward to represent a later assessment when the later value is missing. Observed-case analysis uses available observations for the relevant assessment. These approaches can rely on different assumptions about missing observations and can yield different estimates. The registry record does not report the detailed missing-data rules, the amount or pattern of missingness, or a justification for LOCF. The labels alone are not enough to establish how plausible the assumptions were.

The group sizes shown for each outcome and analysis are not identical. They should be read in the context of the particular endpoint and analysis rather than treated as one common denominator. The registry record does not explain every difference in denominators.

What is the role of the planning illustrations?

In general, a sample-size calculation for a future study depends on assumptions about the effect to detect, variability or event frequency, significance level, allocation, and desired power. The posted planning illustrations use the observed effect or stated fractions of it, a two-sided significance level of 0.05, equal allocation, and a normal approximation. For the binary outcomes, the figures are participants per arm. These are retrospective planning illustrations, not the trial’s original design calculation.

Power is the probability that a planned study would detect an effect of the specified size under the calculation’s assumptions. The 80% and 90% columns describe different target probabilities for a hypothetical future design. They are not probabilities that the observed trial result is correct. The registry record does not report the trial’s own original sample-size assumptions, interim-analysis plan, or full statistical analysis plan.

Why is multiplicity relevant?

When several endpoints, time points, or analysis approaches are considered, the chance of at least one apparently notable result can increase if each is tested without adjustment. In general, multiplicity procedures control or otherwise address that issue. The registry lists 18 outcome measures and reports several secondary outcomes, but the multiplicity approach is not reported in the registry record. Therefore, the unadjusted recalculations should be treated as descriptive and exploratory rather than as a family of confirmatory tests.

The primary endpoint remains the main efficacy question identified in the record. Secondary analyses can show whether findings are consistent across related measures, but they do not automatically confirm the primary result. Nor can a collection of unadjusted p-values establish a single overall conclusion without a prespecified interpretation plan.

11. Confidence Intervals and Precision

The primary estimates are not highly precise: their 95% confidence intervals span values close to no difference as well as values suggesting a more favorable outcome in the active-treatment group. For the LOCF sponsor analysis, the odds-ratio interval is 0.97 to 2.03. For the observed-case sponsor analysis, it is 1.00 to 2.14. The interval limits indicate that the data do not pin down one narrow effect size.

The unadjusted recalculated risk-difference intervals also include zero: -0.006 to 0.146 for LOCF, and -0.011 to 0.141 for observed case. A risk difference of zero corresponds to equal observed proportions. The intervals therefore include little or no separation as well as positive differences. Since the registry flags a discrepancy, the sponsor’s analyses take precedence over these simple recalculations.

In general, a confidence interval expresses statistical uncertainty conditional on the model and analysis assumptions. It does not account for every possible source of uncertainty, such as missing-data assumptions, outcome measurement issues, or selective reporting. The registry record does not report enough detail to assess all of those sources.

Precision also depends on the scale used to express the result. The odds ratio and risk difference describe the same broad comparison in different units; their estimates and intervals should not be compared as though the numeric scales were equivalent. The posted percentages help show the observed group frequencies, while the intervals show how uncertain those estimates and contrasts remain.

The results support a cautious reading: the point estimates favor DFN-15, but the primary sponsor intervals do not rule out an effect near the no-difference value. They also do not establish that the groups are equivalent. A narrower estimate would require more information or a study designed to estimate the effect with greater precision; the appropriate design assumptions are not reported in the registry record.

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 binary outcomes, not total participants across arms. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The registry record does not report the original design assumptions for this trial.

The 80% power column gives the illustrative number of participants per arm for a hypothetical study designed to have an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding figure for a 90% target chance. A higher power target generally requires more participants. Likewise, planning for 75% or 50% of the observed effect means targeting a smaller effect than the full observed estimate; smaller effects need more participants to detect.

The displayed estimates are sensitive to the observed effect used as the starting point. When that estimate is small or uncertain, the resulting planning figures can become very large, and they should not be read as a recommended design without considering the scientific question and justified assumptions. The displayed curve provides a way to see how required sample size changes as the target effect changes; it is an illustration of those assumptions rather than a record of the trial’s recruitment plan.

These figures are planning illustrations, not observed power. They do not tell whether the completed trial had a particular probability of success after seeing its results. The registry record does not report the trial’s original sample-size justification or whether any planned design assumptions changed.

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 = 0.258; treatment proportion p₁ = 0.329; average p̄ = 0.293.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6440 = 1.2622.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6421 = 0.5404.
4. n = (1.2622 + 0.5404)² / (0.0701)² = 660.4, rounded up to 661 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 <- 0.258426966292135                          # control proportion
p1 <- 0.328571428571429                          # 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(3009019)
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 = 661 (80% power), 884 (90% power)
 75% of observed effect: n per arm = 1,154 (80% power), 1,545 (90% power)
 50% of observed effect: n per arm = 2,549 (80% power), 3,412 (90% power)
power.prop.test: 660.4 
Simulated power at n = 661 per arm: 0.801 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s own analyses are reported as Fisher Exact comparisons of odds ratios. For LOCF, the reported odds ratio is 1.40, with a 95% confidence interval of 0.97 to 2.03 and p = 0.075. For observed case, the reported odds ratio is 1.47, with a 95% confidence interval of 1.00 to 2.14 and p = 0.055.

The separate recalculations use posted summary statistics to form simple, unadjusted comparisons. For the primary active-versus-placebo contrasts, they report risk differences of 0.070 for LOCF and 0.065 for observed case, with p-values of 0.072 and 0.095, respectively. These recalculations are not the sponsor’s analysis and do not reproduce all details of the sponsor’s method.

The registry flags a discrepancy between reported results and recalculated results. Accordingly, the sponsor’s own analysis takes precedence when describing the official trial result. The recalculations can still help readers understand the contrast on another scale, but they should not override or be combined with the reported sponsor estimates. Both sets of primary results indicate uncertainty around the effect, and neither should be presented as definitive evidence of a precise difference.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint, but also lists multiple secondary outcomes and reports results across treatment periods and analysis approaches. This creates a multiplicity issue: when many statistical comparisons are made, some may appear notable by chance even if there is no underlying effect. In general, a prespecified strategy can address this through methods such as adjustment, a testing hierarchy, or a clearly defined distinction between confirmatory and exploratory outcomes.

The multiplicity strategy is not reported in the registry record. The record also does not report whether secondary outcomes were intended to be confirmatory, how the many time points and measures were prioritized, or whether any adjustment was made. Consequently, unadjusted secondary p-values should not be read as if each were the sole planned test. The primary endpoint has the clearest stated role, but its interpretation still depends on the sponsor’s reported analysis and the uncertainty in the estimates.

Missing-data handling is another important issue. The primary results are labelled LOCF and observed case, indicating that more than one approach was used. In general, LOCF carries a previous observation forward when a later value is missing, whereas an observed-case analysis relies on available observations. Each approach makes assumptions; their suitability depends in part on why data are missing and how missingness relates to outcomes.

The registry record does not report the amount or pattern of missing data, the detailed rules for applying LOCF, or sensitivity analyses that would show how conclusions change under alternative assumptions. It also does not provide enough information to determine whether missingness differed between groups. These omissions limit assessment of robustness.

The primary population is identified as Full Analysis Set 1, but the registry record does not report a full definition of that set. Analysis populations for all outcomes and the handling of protocol deviations are not described in the record information available for this analysis. Interim analyses and the complete statistical analysis plan are not reported in the registry record. These details should not be inferred from the outcome results.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cystitis (0.4%), abortion spontaneous (0.4%), non-cardiac chest pain (0.4%), pulmonary embolism (0.3%).

The registry reports serious adverse events for DB1 and DB2 separately and gives an overall row. In DB1, serious events were reported for 2 participants in the placebo group and 1 in the DFN-15 group. In DB2, the corresponding counts were 0 and 1. The overall row reports 4 serious adverse events among 572 at risk. These are counts as recorded, not a comparison adjusted for exposure time or other differences between periods.

No deaths are reported in any listed group or in the overall row. The registry also reports other adverse events separately from serious adverse events; those categories should not be conflated. Serious adverse events are relatively uncommon in the posted record, so small changes in counts can materially alter a simple comparison. These data alone do not establish that the groups have equivalent safety profiles.

The registry lists several serious-event terms with percentages, but the event counts do not provide a complete assessment of causality, timing, recurrence, or duration. The information does not establish whether an event was caused by study drug. Safety findings should be interpreted in the context of the trial’s follow-up and collection procedures, whose full details are not reported in the registry record.

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

The primary results show higher observed pain-free percentages for DFN-15 than placebo under both LOCF and observed-case reporting. The sponsor’s reported confidence intervals and p-values, however, leave uncertainty around the size of the contrast and do not meet the conventional 0.05 threshold. The results therefore support neither a claim of a precisely established effect nor a claim that there is no effect.

The endpoint is narrowly defined: pain-free status at 2 hours after dosing during the first treated double-blind period. It does not establish how participants felt at other times, whether relief persisted, whether associated symptoms resolved, or how outcomes varied across later attacks. The registry lists separate outcomes for some of these questions, but secondary results carry additional uncertainty and lack a reported multiplicity strategy.

The posted group percentages are estimates from the analyzed participants, not guarantees of what would occur for any individual. Confidence intervals describe statistical uncertainty under the analysis assumptions, not the full range of individual experiences. The record does not include enough detail to assess every aspect of missing data, population definition, or analysis implementation.

The results also do not establish a full benefit-risk balance. Adverse-event counts are available, including serious events and deaths, but the registry record does not provide all context needed to infer causality or compare safety comprehensively. Nor does the information establish outcomes beyond the studied population and protocol context.

In general, a trial result is most informative when read with its endpoint definition, analysis population, uncertainty, and prespecified statistical plan. Here, the sponsor’s analysis takes precedence over unadjusted recalculations, and the flagged discrepancy warrants keeping those analyses distinct. The registry record does not report several details that would strengthen assessment of robustness, including the original design assumptions and full missing-data and multiplicity plans.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate alone is not enough. The observed primary percentages are directionally different, but the sponsor’s confidence intervals extend to values compatible with little or no separation. The accompanying p-values are near the conventional threshold, emphasizing that statistical evidence is not a simple yes-or-no property of the estimated effect.

It also demonstrates how analysis choices affect interpretation. The registry presents LOCF and observed-case results and reports sponsor analyses on the odds-ratio scale. Simple recalculations from summary counts use a different, unadjusted approach and do not exactly match the sponsor’s reported values. The record flags this discrepancy, so the official sponsor results take precedence; the supplementary calculations are not interchangeable with them.

The study also raises general questions about multiplicity and missing data. A primary endpoint is accompanied by many secondary measures and time points, but the registry record does not report a multiplicity strategy. The LOCF label signals an approach to missing observations, yet detailed rules and missingness patterns are not reported. Those details matter because apparent consistency across many measures can be overstated when analyses are not interpreted as a planned family.

Finally, the planning illustrations show how sample-size requirements depend on the effect assumed for a future study. They are not the original study’s design calculation and are not observed power. Keeping observed estimates, sponsor analyses, retrospective planning, and safety counts conceptually separate is essential to reading a clinical-trial record accurately.

19. Limitations

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

Several trial-specific details needed to evaluate design and analysis are not reported in the registry record. These include the randomization procedure, allocation concealment, who was masked, the original sample-size justification, and the full statistical analysis plan. The record does not state whether interim analyses were planned or conducted.

The primary outcome is presented under LOCF and observed-case approaches, but the detailed missing-data rules, missingness patterns, and sensitivity analyses are not reported. The record identifies Full Analysis Set 1 but does not fully define that analysis population in the information. Differences in denominators across outcomes and analyses therefore cannot be fully explained from the registry record.

The registry flags a discrepancy between sponsor analyses and simple unadjusted recalculations. The sponsor’s reported results should take precedence, but the discrepancy limits how directly the recalculated comparisons can be used to validate the official analyses. The sponsor reports odds ratios from Fisher Exact analyses, whereas the recalculations provide unadjusted contrasts from summary counts.

Multiplicity is an additional limitation because several outcomes and assessment periods are reported, while the registry record does not describe any adjustment or testing hierarchy. Secondary results should consequently be treated with caution. The record also provides limited context for the serious adverse-event counts, including no detailed causal assessment or event-level timing information. These limitations affect interpretation of precision and robustness; they do not, by themselves, determine the direction of the treatment effect.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy, Tolerability, and Safety of DFN-15 — NCT03009019.
• Registry record last updated 2023-01-10; status last verified 2022-12.
• Results first posted 2023-01-10.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed phase 3, randomized, triple-masked, parallel-group, multicenter study of DFN-15 versus placebo in episodic migraine with or without aura. Enrollment was 631. The listed study start is 2016-12 and primary completion is 2017-11.

The primary endpoint was the percentage pain-free 2 hours after dosing during the first treated double-blind period, with Full Analysis Set 1 identified as the analysis population. Sponsor-reported LOCF and observed-case analyses showed higher observed percentages in the active group, but their confidence intervals and p-values leave uncertainty about the size of the difference. The registry flags a discrepancy with simple recalculations, so the sponsor’s analyses take precedence.

The record lists numerous secondary outcomes and reports serious adverse-event counts, but multiplicity handling, detailed missing-data procedures, original sample-size assumptions, and several other design and analysis details are not reported in the registry record.