Diphenhydramine for Acute Migraine: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Diphenhydramine for Acute Migraine (NCT01825941), a randomized phase 4 study. The primary outcome is Number of Participants With Sustained Headache Relief Assessed by Self-evaluation.

2. Clinical Question

3. Trial Design

The registry describes a phase 4, randomized, parallel-group trial with quadruple masking. It lists Montefiore Medical Center as sponsor and records the study as completed. The study concerned acute migraine and compared metoclopramide plus diphenhydramine with metoclopramide plus placebo. The registry lists enrollment as 208.

The brief summary describes concealed assignment and blinding of participants and researchers. It also says efficacy outcomes and adverse events were assessed every half hour for two hours in the emergency department, followed by telephone contact 48 hours after medication administration. The primary outcome description places the telephone assessment 48 hours after discharge. These descriptions establish the planned assessment approach, but further details on how calls were completed or outcomes adjudicated are not reported in the registry record.

The summary states that a sample-size calculation based on pilot data indicated a need for 374 participants. It also describes an interim analysis after 200 participants had been enrolled, with the goal of assessing lack of conditional power. The registry record does not report the results of that interim analysis, whether it affected trial conduct, or the original statistical analysis plan. The posted outcome groups list 100 participants for the diphenhydramine group and 103 for the placebo group. The record does not explain the relationship between these outcome counts, the enrollment entry, and the different safety denominators.

Trial dates are recorded as starting in 2013-04 and reaching primary completion in 2014-12. The registry lists one outcome measure and zero posted analyses. Details such as the method of sequence generation, the specific masking roles, and the analysis population are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

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 Number of Participants With Sustained Headache Relief Assessed by Self-evaluation, measured over up to 2 hours in Emergency Department, 48 hours after discharge from Emergency Department.

The primary endpoint counts participants with sustained headache relief, rather than measuring the average amount of pain reduction. A participant met the definition by reporting a headache level of mild or none within two hours and maintaining mild or none for 48 hours. Self-evaluation was solicited every half hour in the emergency department and again by telephone 48 hours after discharge.

This endpoint combines an early response with its persistence. Requiring both may be useful when the clinical question concerns whether relief is sustained, rather than whether headache intensity changes briefly after treatment. At the same time, a binary endpoint reduces each participant’s experience to whether the definition was met or not met. It does not show how far pain changed for those who did not meet the threshold, or when relief began within the assessment period.

The endpoint depends on repeated self-reports and a later telephone assessment. The registry describes the assessment schedule and definition, but does not report missing-response counts, handling of incomplete assessments, or rules for classifying participants without a 48-hour report. Those details matter because incomplete follow-up can affect which participants are counted as having sustained relief. The posted results should therefore be read as counts meeting the registry’s stated definition, not as a complete description of every participant’s headache course.

7. Results Posted in the Registry

• Metoclopramide + Diphenhydramine: 40.0% (40/100) versus 36.9% (38/103) on control; risk difference 3.1 percentage points (95% CI -10.3 to 16.5), risk ratio 1.08 (0.77–1.54); unadjusted two-proportion z-test p = 0.649.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the risk difference describe?

The risk difference compares the proportion meeting an endpoint in one group with the proportion in another. For this trial, the endpoint was sustained headache relief, defined as mild or no headache within two hours and maintaining that level for 48 hours. A positive estimate of 0.031 indicates that the observed proportion was higher in the diphenhydramine group than in the placebo group. The estimate is an absolute contrast on the probability scale, not a relative increase. It summarizes the observed groups; interpretation as a treatment effect depends on the trial design, follow-up, and analysis.

What is a confidence interval?

General: A confidence interval describes the range of effect estimates reasonably compatible with the data under the statistical method used. It conveys precision as well as direction. When an interval for a risk difference includes zero, the data do not rule out no difference at the conventional confidence level associated with that interval. An interval extending on both sides of zero also allows for differences in either direction. The registry’s interval crosses zero, so the estimate does not precisely distinguish a positive difference from a negative one. The interval is not a guarantee that the true effect lies within its endpoints, nor does it show the probability of a particular effect.

How should the p-value be read?

The registry reports an unadjusted p-value of 0.649. General: A p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test assumptions held. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. A larger p-value is not proof of no effect, just as a smaller p-value alone would not establish importance or eliminate bias. The registry record does not report the test specification or an adjusted p-value; the posted value is explicitly unadjusted.

What do risk ratios and odds ratios add?

The comparison record also gives a risk ratio of 1.084, with a confidence interval from 0.765 to 1.536, and an odds ratio of 1.14, with a confidence interval from 0.647 to 2.008. General: A risk ratio compares the event probabilities between groups, while an odds ratio compares event odds. Both are relative measures, unlike the absolute risk difference. Their confidence intervals include the no-association value of one. They therefore also reflect uncertainty about direction and size. Relative measures can look different from absolute measures because they use different scales; neither should be interpreted in isolation from the event counts and the endpoint definition.

Why does randomization matter?

General: Random assignment is intended to make treatment groups comparable, on average, with respect to factors known and unknown before assignment. Concealed assignment can reduce the chance that enrollment decisions are influenced by the upcoming group. Masking can reduce the influence of treatment knowledge on care, reporting, and assessment. The registry describes the trial as randomized and quadruple-masked, and its summary says assignment was concealed and participants and researchers were blinded. The exact roles covered by quadruple masking, sequence-generation method, and concealment procedures are not reported in the registry record. These design labels describe the intended safeguards; they do not by themselves document how completely each safeguard was implemented.

Why can over-dispersion matter?

General: Over-dispersion means observed variability is greater than a model expects. It is particularly relevant when outcomes are counts whose variation may not fit a simple probability model. Extra variability can make standard errors too small if the analysis assumes less variation than is present, which can make confidence intervals too narrow and tests too optimistic. This trial’s primary outcome is a binary participant count, and the registry provides no model specification or dispersion estimate. The registry record does not report that an over-dispersion adjustment was used. The concept is relevant to count-based analysis generally, but no conclusion about over-dispersion in this trial can be drawn from the posted record.

What is not documented about the analysis?

The registry reports one outcome measure and zero posted analyses. It supplies the group counts and an unadjusted comparison, but does not report the statistical test, covariate adjustment, handling of missing outcome reports, analysis population, or protocol deviations. The summary mentions an interim analysis intended to assess lack of conditional power, but its results and any effect on the final analysis are not reported in the registry record. These omissions prevent a full audit of the analysis pathway. The posted estimates remain interpretable as the registry’s reported summaries, but their relationship to a prespecified analysis plan cannot be verified from this record.

10. Confidence Intervals and Precision

The risk-difference estimate is 0.031, and the associated confidence interval extends from below zero to above zero. This interval includes no difference and permits effects in either direction. Its breadth signals that the data do not pin down the size of the contrast precisely. The interval should be read alongside the group counts: 40 of 100 participants in the diphenhydramine group and 38 of 103 in the placebo group met the endpoint.

The relative-effect summaries tell a similar uncertainty story. The risk ratio is 1.084, with an interval from 0.765 to 1.536; the odds ratio is 1.14, with an interval from 0.647 to 2.008. Both intervals include one, the value corresponding to no relative difference. These measures do not remove uncertainty merely by expressing the comparison on a relative scale.

The unadjusted p-value is 0.649. It is consistent with the broad uncertainty reflected in the intervals, but it should not replace them. Neither the p-value nor the point estimate alone establishes the presence, absence, or practical importance of an effect. The registry does not report a target difference for interpretation, a threshold for clinical importance, or an equivalence margin.

Precision is also affected by the available outcome information and its completeness. The registry lists 100 and 103 participants in the primary outcome groups, while separate safety denominators are recorded. It does not report the flow of participants through follow-up or the handling of missing primary assessments. The confidence interval quantifies sampling uncertainty under its method; it does not account automatically for possible missing-data or measurement biases.

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 a report of the trial’s original design calculation. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row considers detecting the stated fraction of the observed effect. The figures are participants per arm, not total participants or total events.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the model assumptions are correct. The 90% power column gives the corresponding number per arm for a design with a 90% chance. These are prospective planning quantities, not a measure of what the completed trial achieved. The calculations are not observed power.

The rows describe planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller effects require more participants to detect under the same assumptions. For example, planning for 75% of the observed effect requires 6,815 participants per arm for 80% power and 9,123 per arm for 90% power; planning for 50% requires 15,274 per arm for 80% power and 20,447 per arm for 90% power. The figures are illustrations, not recommendations or evidence that an effect of that size is real.

The registry’s own brief summary says a calculation based on pilot data indicated a need for 374 participants and describes an interim analysis after 200 participants to assess lack of conditional power. The original calculation’s detailed assumptions and the interim results are not reported in the registry record. Those trial-specific statements should not be conflated with the separate planning illustrations based on the observed effect.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.369; treatment proportion p₁ = 0.400; average p̄ = 0.384.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6880 = 1.3484.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6876 = 0.5787.
4. n = (1.3484 + 0.5787)² / (0.0311)² = 3,847.6, rounded up to 3,848 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 <- 0.368932038834951                          # control proportion
p1 <- 0.4                          # 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(1825941)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 3,848 (80% power), 5,151 (90% power)
 75% of observed effect: n per arm = 6,815 (80% power), 9,123 (90% power)
 50% of observed effect: n per arm = 15,274 (80% power), 20,447 (90% power)
power.prop.test: 3847.6 
Simulated power at n = 3,848 per arm: 0.803 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one outcome measure and zero posted analyses. It does not list secondary outcomes in the results record. With only one posted outcome, the record does not describe a set of multiple posted efficacy outcomes requiring a reported multiplicity adjustment. However, the registry record does not report the full protocol or statistical analysis plan, so it is not possible to establish whether additional outcomes or analyses were planned, whether any were omitted, or whether multiplicity procedures were prespecified.

Multiplicity arises when many outcomes, time points, subgroups, or comparisons are tested. Repeated testing can increase the chance of at least one apparently unusual result by chance. General statistical approaches can control that risk, but no adjustment method is reported for this trial. The posted p-value is unadjusted. It should not be described as adjusted for multiple comparisons.

Missing data are important for this endpoint because it requires repeated self-reports in the emergency department and a later telephone assessment. The registry describes the assessment schedule but does not report how many primary outcome assessments were missing, whether participants were unreachable, or what rules were used to classify incomplete records. It also does not state whether any imputation, sensitivity analysis, or missing-at-random assumption was used. Therefore, the effect of missing outcome information on the reported comparison cannot be assessed from the registry record.

The analysis population is not reported in the registry record. In particular, the record does not say whether the primary comparison used all randomized participants, only participants with an available outcome, or another defined group. The outcome group counts are reported, but the flow from randomization to those counts and reasons for any exclusions are not described. The brief summary’s mention of an interim analysis does not provide its methods or results. These gaps limit assessment of whether the final comparison followed an intention-to-treat approach or another prespecified strategy.

14. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse-event entries report zero affected participants in each group: 0 among 104 at risk in the metoclopramide plus diphenhydramine group, and 0 among 103 at risk in the metoclopramide plus placebo group. The death count is also 0 in each group. These are reported counts, not proof that serious events or deaths could not occur. The record does not provide additional detail on surveillance or event definitions.

Other adverse events are listed for 25 participants in the diphenhydramine group and 21 in the placebo group, with 104 at risk in each group for that category. The registry does not provide a breakdown of those events in the posted terms. The safety records use denominators that differ from the primary outcome group count for the diphenhydramine group; participant flow or the reason for that difference is not reported in the registry record.

These safety counts are descriptive. They do not establish that the groups had equivalent safety, and no inferential comparison is posted. Rare or delayed events may not be characterized by these counts, and the registry does not report follow-up completeness or event-specific severity beyond the serious-event classification.

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

The registry’s primary result is a comparison of the number of participants meeting a defined sustained-relief endpoint. The recorded counts are 40 of 100 in the metoclopramide plus diphenhydramine group and 38 of 103 in the metoclopramide plus placebo group. The estimated risk difference is positive, but its confidence interval crosses zero and extends in both directions. The unadjusted p-value is 0.649. Together, these statistics show that the posted data do not precisely determine the direction or size of a difference.

This result does not establish that adding diphenhydramine causes greater sustained relief, nor does it establish that there is no effect. A non-significant p-value is not proof of equivalence. The registry does not report an equivalence or noninferiority design, a clinically important threshold, or a prespecified decision rule for interpreting the size of the difference. The estimate and its uncertainty should be considered together rather than treating the p-value as a verdict.

The endpoint captures a particular outcome: mild or no headache within two hours, maintained for 48 hours. It does not describe every aspect of migraine, the amount of improvement among those who did not meet the threshold, or other outcomes that were not posted. The record includes adverse-event counts but does not provide detailed event terms or a comparative safety analysis.

Interpretation is further constrained by the absence of reported analysis-population details, missing-data methods, and interim-analysis results. The registry describes randomization, concealment, and masking, but does not report enough implementation detail to independently evaluate these features. The posted results are therefore best understood as an uncertain estimate for the registry-defined endpoint, rather than a complete account of treatment effects or a basis for individual medical decisions.

16. Why This Trial Matters Statistically

This trial illustrates why a point estimate, its uncertainty, and the outcome definition should be read together. The observed group counts are close, and the risk-difference estimate is small on its absolute scale. Yet the confidence interval crosses zero and allows differences in either direction. The unadjusted p-value alone cannot resolve that uncertainty, and it cannot establish equivalence. The example shows how an apparently straightforward comparison can remain inconclusive about the population effect.

The endpoint also demonstrates a design choice with statistical consequences. Sustained relief is a binary outcome that combines early improvement and persistence through 48 hours. That definition is directly tied to the study question, but it discards variation in symptom change among participants who do not meet the threshold. A different outcome definition could capture a different feature of the clinical course, so the endpoint needs to be considered before interpreting the comparison.

The registry’s sample-size illustration makes another point: planning needs depend on the effect a study aims to detect. Under the listed assumptions, planning to detect a smaller fraction of the observed effect requires more participants per arm. Those calculations are not observed power, and they are separate from the registry summary’s pilot-based calculation and interim-analysis description. Keeping these planning concepts distinct prevents the observed result from being misrepresented as evidence that a study was adequately powered for every possible effect.

Finally, the record highlights the importance of transparent reporting. Analysis populations, missing outcomes, interim results, and detailed methods are not reported. Without them, readers can interpret the posted estimate and interval but cannot fully reconstruct the analysis or evaluate all potential sources of uncertainty. Statistical interpretation depends both on the numerical result and on clear documentation of how it was produced.

17. 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 gives limited information about who entered the trial. It describes people presenting to the Montefiore emergency room with acute migraine and notes screening for medication contraindications and non-migraine causes of headache. Further eligibility criteria, participant characteristics, and the number screened or excluded are not reported. The results therefore have limited documented context for judging applicability beyond the enrolled setting.

The primary endpoint depends on self-reported headache levels during repeated emergency-department assessments and a telephone assessment 48 hours after discharge. The registry defines sustained relief, but does not report the completeness of those assessments, the handling of unavailable telephone follow-up, or the method used to resolve incomplete records. These omissions make it difficult to assess potential effects of missing reports or measurement variation.

Outcome counts, enrollment, and safety denominators are reported in separate entries, but participant flow and reasons for denominator differences are not reported in the registry record. The record also does not describe protocol deviations, adherence to the assigned infusion, or co-interventions. No subgroup or secondary outcome results are posted, and zero analyses are listed.

The brief summary describes a pilot-based target of 374 participants and an interim analysis after 200 participants, but the interim findings, stopping decisions, and detailed original design assumptions are not reported. The statistical test, analysis population, covariate adjustment, and missing-data methods are also not reported. These limits do not negate the posted result, but they restrict how completely its robustness and generalizability can be assessed.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Diphenhydramine for Acute Migraine — NCT01825941.
• Registry record last updated 2018-07-31; status last verified 2018-07.
• Results first posted 2018-06-08.
• 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.

21. Record Summary

The completed phase 4 trial randomized participants in a parallel-group design and was listed as quadruple-masked. It compared intravenous metoclopramide plus diphenhydramine with metoclopramide plus placebo for acute migraine. The primary endpoint counted participants who reached mild or no headache within two hours and maintained that level for 48 hours.

The posted outcome counts were 40 of 100 in the diphenhydramine group and 38 of 103 in the placebo group. The reported risk difference was 0.031, with an interval crossing zero, and the unadjusted p-value was 0.649. Serious adverse events and deaths were recorded as 0 in both groups; other adverse-event counts were also posted.

The registry does not report the analysis population, missing-data methods, detailed analysis plan, or interim-analysis results. The observed comparison is uncertain and does not establish either an effect or equivalence.