Dexamethasone for Migraine - Dose Comparison: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dexamethasone for Migraine - Dose Comparison (NCT04112823), a randomized phase 4 study. The primary outcome is Number of Subjects With Headaches Who Have Sustained Headache Relief for 48 Hours.

2. Clinical Question

3. Trial Design

NCT04112823 is listed as a completed phase 4 randomized, quadruple-masked, parallel-group study sponsored by Montefiore Medical Center. The registry records enrollment of 209 participants, a start date of 2019-12-22, and primary completion on 2022-12-31. The trial compared two intravenous dexamethasone doses: 4mg and 16mg. The registry summary states that all patients also received metoclopramide. Thus the randomized comparison concerns dose level within a shared treatment setting.

The primary outcome was a participant count: the number achieving sustained headache relief for 48 hours. The registry defines relief as headache intensity of none or mild, with no additional rescue therapy throughout the 48-hour follow-up. The posted primary outcome counts are 35 of 102 for dexamethasone 4mg and 42 of 102 for dexamethasone 16mg. The registry notes that two participants in the 4mg group and three in the 16mg group did not complete 48-hour follow-up and had no 48-hour data collected. It does not report how those missing outcomes were handled in the analysis.

Five secondary outcomes are posted, covering relief within two hours, additional headache medication in the emergency department, preference for the same medication for a subsequent headache, days with headache, and additional medication after emergency-department discharge. The registry lists six outcome measures in total and five analyses. The design record does not report the allocation ratio, the sequence-generation process, masking procedures, or the original sample-size justification. Those details are not inferred from the observed arm counts or from the planning illustrations.

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: Altogether, 1823 patients were screened and 209 were randomized into the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Two subjects in the Dexamethasone 4mg arm and 3 subjects in the Dexamethasone 16mg arm did not complete their 48 hour follow up. As such, 48 hour data was not collected from these subjects.

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 Subjects With Headaches Who Have Sustained Headache Relief for 48 Hours, measured over 48 hours.

The primary endpoint counts participants who achieved sustained headache relief during the 48 hours after treatment. Under the registry definition, a participant had to report headache intensity of none or mild and remain at that level without needing additional rescue therapy across the entire follow-up period. This is a binary outcome at the participant level: each person either meets the stated definition or does not.

A sustained endpoint captures more than an early change in symptoms. Its requirement that relief continue without rescue therapy makes duration and maintenance part of the outcome. The registry also lists relief within two hours as a separate secondary outcome, distinguishing an early response from the longer 48-hour criterion. These endpoints address different time windows and should not be treated as interchangeable.

The primary measure is expressed as a count of participants, with each arm’s outcome count interpreted against its reported denominator. The posted results give 35 participants with sustained relief among 102 in the 4mg group and 42 among 102 in the 16mg group. The registry reports that two and three participants, respectively, lacked 48-hour follow-up data. Because the record does not state how those missing outcomes entered the analysis, the counts should be read alongside that limitation rather than assumed to represent a particular missing-data strategy. The endpoint describes the registry’s specified outcome; it does not by itself establish that one dose is superior.

7. Results Posted in the Registry

• Dexamethasone 16mg: 41.2% (42/102) versus 34.3% (35/102) on control; risk difference 6.9 percentage points (95% CI -6.4 to 20.1), risk ratio 1.20 (0.84–1.71); unadjusted two-proportion z-test p = 0.312.

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.

Number of Subjects With Headache Who Have Relief Within Two Hours of Medication Administration

• 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:
  • Dexamethasone 16mg: 78.1% (82/105) versus 74.0% (77/104) on control; risk difference 4.1 percentage points (95% CI -7.5 to 15.6), risk ratio 1.05 (0.91–1.23); unadjusted two-proportion z-test p = 0.492.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dexamethasone 16mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the assessment beyond sustained relief at 48 hours. They cover early relief, additional medication in the emergency department, preference for the same medication at a subsequent headache, days with headache, and additional medication after emergency-department discharge. These outcomes concern different aspects of experience and different time windows, so they need not move in lockstep with the primary endpoint.

The posted comparison for relief within two hours has an unadjusted p-value of 0.492, and its confidence interval spans no difference. This pattern is consistent with uncertainty rather than a clear separation between the dose groups. The remaining secondary outcomes are listed in the registry, but their result details and corresponding estimates are not reported in the analysis information used for this interpretation. Consequently, no overall directional pattern across all secondary outcomes can be established from the record.

Secondary outcomes can help describe whether the primary finding is accompanied by differences in related measures. They do not independently confirm the primary result simply because they were measured. When several outcomes are tested, the chance of at least one apparently unusual finding can increase. Statistical methods that account for multiplicity can address that issue, but no such procedure is reported in the registry record. The available secondary p-value is unadjusted, and the record does not say whether other secondary comparisons were prespecified or how their results were selected for reporting.

For these reasons, secondary outcomes carry less weight than a clearly specified primary analysis when assessing the main trial question. They should be treated as supporting context, with attention to their definitions, missingness, and analysis methods. The registry’s outcome list alone does not establish whether a secondary result is robust or clinically important.

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

• Number of Subjects With Headache Who Have Relief Within Two Hours of Medication Administration
• Additional Headache Medication in the ED
• Patient Preference for Receiving the Same Medication for a Subsequent Headache
• Number of Days With Headache
• Use of Additional Headache Medication After ED Discharge

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary comparison is an unadjusted analysis of a binary outcome. Each participant is classified according to whether the registry’s sustained-relief definition was met. The result can be expressed as an event count in each arm, as a risk within each arm, or as a contrast between arms. The arm counts are 35 of 102 for dexamethasone 4mg and 42 of 102 for dexamethasone 16mg. The recalculation uses the posted summary counts and does not incorporate covariate adjustment.

What does a risk difference describe?

A risk difference compares the proportion of participants with the event in one group with the proportion in the other group. A positive value in a comparison defined as 16mg relative to 4mg means the observed event proportion is higher in the 16mg group; a negative value means it is lower. Unlike a ratio, this measure is expressed on an absolute scale. For this outcome, the recalculated estimate is positive, while its interval extends across zero. The interval therefore includes both a possible positive difference and a possible negative difference under the calculation’s assumptions.

Why are ratios also reported?

A risk ratio compares the event risk in one arm with the event risk in the other, while an odds ratio compares the odds. Ratios use a relative scale rather than the absolute difference scale. Their interpretation depends on which group is the reference and on whether the reported quantity is a risk or odds ratio. The recalculated results include ratio estimates, but the values and intervals have more decimal places than the permitted reporting precision, so they are not repeated. The sponsor’s analysis is labeled Risk Ratio (RR), yet its reported value and confidence limits are presented as 7 and -6 to 20. Since the method and p-value are absent, the registry record does not clarify the scale or calculation behind that presentation.

What does a confidence interval contribute?

A confidence interval communicates uncertainty in an estimate. In general, a narrower interval indicates greater precision, while a wider interval is compatible with a broader range of effects. For a risk difference, zero is the null value indicating no difference between groups. The recalculated primary interval includes zero, so the posted summary statistics do not exclude no difference at the stated confidence level. This is not the same as proving no effect: the interval also permits effects in either direction. A p-value gives a related measure of how compatible the observed data are with a specified null model, given the analysis assumptions; it is not the probability that the null hypothesis is true. The primary unadjusted p-value is 0.312.

Why can dispersion matter?

Dispersion is a general concern when analyzing outcomes whose variability exceeds what a model assumes. Extra variation can make standard errors too small if the model does not account for it, leading to intervals that are too narrow and tests that appear too decisive. The primary endpoint is a participant count with a binary event definition, rather than a continuous measurement or a recurrent event count. The registry lists no dispersion estimate for this endpoint. No over-dispersion model or other adjustment is reported, so none should be attributed to the trial analysis.

What do the analysis labels establish?

The registry classifies the comparison as a superiority analysis and reports a 95% confidence interval for its sponsor analysis. It does not report that analysis’s method or p-value. The recalculation is explicitly unadjusted and is based on the arm-level counts. These are distinct descriptions of statistical work. Without a documented analysis method, the sponsor result cannot be reconstructed from the record alone. The absence of a reported method also means that assumptions such as covariate adjustment, stratification, or a particular missing-outcome procedure cannot be inferred.

In general, randomized comparisons aim to use allocation to make the groups comparable on average, but randomization does not eliminate uncertainty in the observed estimate. The registry identifies the study as randomized, but does not report the sequence-generation or allocation-concealment details. Likewise, quadruple masking is recorded, but the identities of the masked parties and operational procedures are not described. The statistical interpretation should therefore rest on the characteristics actually recorded: randomized parallel groups, the posted event counts, the recalculated unadjusted comparison, and the limits of the missing analysis details.

11. Confidence Intervals and Precision

The primary comparison has limited precision. The recalculated risk-difference confidence interval extends from a negative value to a positive value, crossing the null value of zero. This means the data are compatible with a range that includes the possibility of fewer participants achieving sustained relief in the 16mg group, no difference, or more participants achieving relief in that group. The unadjusted p-value is 0.312, which does not resolve that uncertainty.

A confidence interval should be read as a range of estimates compatible with the data and the method, not as a guarantee that the true effect lies inside it. In general, interval width reflects both the observed data and the assumptions used to calculate uncertainty. Here the primary arm counts are 35 of 102 and 42 of 102. The record also notes that five participants did not complete 48-hour follow-up, with two in the 4mg group and three in the 16mg group. The registry does not report how those missing outcomes were handled, which limits assessment of the interval’s relationship to the full enrolled population.

The secondary comparison for relief within two hours also has an interval spanning no difference, and its unadjusted p-value is 0.492. These results do not provide a precise separation between groups. The sponsor’s primary analysis reports a 95% interval from -6 to 20 alongside a Risk Ratio label; the record gives no method to clarify the scale. That presentation should not be conflated with the unadjusted risk-difference interval. Overall, the posted statistics allow uncertainty about both the direction and the size of any difference.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations describe participants per arm for the binary outcomes; they are not totals across both arms and are not total event counts. The assumptions are 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 a stated fraction of the observed effect. These calculations are planning illustrations based on the observed effect, not the trial’s original design justification. The original design assumptions are not reported in the registry record. This is not observed power.

For the primary outcome, planning for 100% of the observed effect gives 783 participants per arm for 80% power and 1,047 participants per arm for 90% power. Planning for 75% of the observed effect gives 1,379 participants per arm for 80% power and 1,845 participants per arm for 90% power. Planning for 50% of the observed effect gives 3,072 participants per arm for 80% power and 4,112 participants per arm for 90% power.

The 80% power column describes the planned number per arm under which the assumed effect would be detected by the specified test in 80% of repeated studies, if the assumptions held. The 90% column applies the same idea at a higher chance of detecting that assumed effect, so it requires a larger planned sample. These are conditional planning statements, not probabilities that the observed result is correct.

The observed effect is only an estimate and may be unstable, especially when the interval is broad. The smaller-effect rows illustrate that a study designed to detect a more modest difference needs more participants per arm. The figures should not be read as evidence that the trial was inadequately designed: the registry does not report the original target effect or sample-size rationale. They instead show how planning requirements change under the stated illustrative assumptions.

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 = 0.343; treatment proportion p₁ = 0.412; average p̄ = 0.377.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6855 = 1.3436.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6838 = 0.5755.
4. n = (1.3436 + 0.5755)² / (0.0686)² = 782.0, rounded up to 783 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 <- 0.343137254901961                          # control proportion
p1 <- 0.411764705882353                          # 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(4112823)
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 = 783 (80% power), 1,047 (90% power)
 75% of observed effect: n per arm = 1,379 (80% power), 1,845 (90% power)
 50% of observed effect: n per arm = 3,072 (80% power), 4,112 (90% power)
power.prop.test: 782 
Simulated power at n = 783 per arm: 0.798 (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 registry’s primary sponsor analysis is labeled Risk Ratio (RR), reports a value of 7, and gives a 95% confidence interval from -6 to 20. It does not report a p-value or name the statistical method. The posted arm counts are 35 of 102 for dexamethasone 4mg and 42 of 102 for dexamethasone 16mg. A separate unadjusted recalculation from those counts compares the groups using a risk difference and reports an unadjusted p-value of 0.312. The registry does not flag a discrepancy between the sponsor analysis and the recalculation.

The sponsor result and the recalculation use differently labeled measures, and the record does not explain the sponsor result’s scale or method. In particular, the reported interval includes negative values despite the Risk Ratio label. That makes it inappropriate to treat the two estimates as interchangeable or to infer an undocumented conversion. The recalculation offers a transparent unadjusted comparison of the posted counts; it does not reconstruct the sponsor’s analysis.

Because the registry does not report the sponsor method, its handling of missing 48-hour outcomes, or a p-value, those aspects cannot be assessed from the record. The comparison should retain both pieces of information with their limitations: the sponsor analysis as recorded and the unadjusted count-based recalculation. Neither supplies a precise basis for declaring a difference between doses.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes or makes several statistical comparisons. In general, the more tests considered, the greater the chance that at least one result may appear notable by chance under a collection of null effects. Common approaches include adjusting significance thresholds or using a prespecified hierarchy of outcomes, but the registry record does not report a multiplicity strategy. It also does not report whether the secondary comparisons were adjusted, whether a testing hierarchy was used, or how the five listed analyses relate to the six outcome measures.

The primary endpoint has a 48-hour follow-up requirement, and the registry specifically notes missing 48-hour data for two participants in the 4mg arm and three in the 16mg arm because they did not complete follow-up. The analysis population is not reported. The record does not state whether those participants were excluded, treated as not achieving relief, imputed, or handled through another method. The posted arm counts have denominators of 102 in each group, but the record does not explain how those denominators relate to the participants with missing follow-up or to the total enrollment.

These omissions matter because missing outcomes can affect both the estimated comparison and its uncertainty, particularly if the probability of missing data is related to the outcome. In general, an analysis based only on observed outcomes relies on assumptions about how missingness relates to unobserved outcomes. A sensitivity analysis can test how conclusions change under alternative assumptions, but none is reported in the registry record.

The registry identifies randomization and quadruple masking, but does not report the allocation sequence process, analysis population definition, protocol deviations, or a detailed statistical analysis plan. The exact masked roles and procedures are also not reported. These details are relevant to judging potential sources of bias and to reproducing the reported analysis. Their absence does not demonstrate that a particular problem occurred; it limits what can be verified from the posted record.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cerebellar stroke (1.0%), hyperglycemia (1.0%).

The serious adverse event figures are reported separately by treatment group. For dexamethasone 4mg, the registry lists 2 serious adverse events among 104 participants at risk; for dexamethasone 16mg, it lists 0 among 105 at risk. The registry also lists 22 other adverse events among 104 at risk in the 4mg group and 24 among 105 at risk in the 16mg group. No deaths are reported in either group. The listed serious-event terms are Cerebellar Stroke and Hyperglycemia, each reported as 1.0%.

These are descriptive counts from the registry, not a comparative safety analysis. The record does not report a statistical test, uncertainty interval, event-level timing, severity details beyond the serious-event designation, or a causal assessment. Counts at risk for safety differ from the denominators used for the primary outcome, and the registry’s reason for that difference is not explained. The event figures should therefore be read as the posted safety record, not as precise estimates of comparative risk or proof that an event was caused by a particular dose.

Rare serious events can be difficult to compare reliably in a trial of this size because a small number of events gives limited information about between-group differences. This is a general statistical limitation, not a conclusion that the observed events are or are not related to treatment.

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

The result describes how often the registry-defined 48-hour sustained-relief outcome was recorded in each randomized group: 35 of 102 participants with dexamethasone 4mg and 42 of 102 with dexamethasone 16mg. The count was higher in the 16mg group, and the unadjusted recalculation points in that direction. However, the confidence interval spans the null and the unadjusted p-value is 0.312. The data do not precisely determine whether there is a difference, or how large any difference might be.

This is not proof that the doses are equivalent, nor is it proof that they differ. A non-significant result can arise when a true effect is small, when estimates are imprecise, or when no effect exists. The posted information does not distinguish among those possibilities. The planning illustrations indicate that detecting smaller effects would require more participants per arm under their stated assumptions, but they are not a retrospective measure of how likely this trial was to detect an effect.

The scope is also specific. Participants received intravenous dexamethasone at one of the two recorded doses, and the registry summary says everyone also received metoclopramide. The primary outcome concerns relief maintained for 48 hours without additional rescue therapy, not every possible outcome of acute migraine care. Missing 48-hour follow-up is recorded for two participants in the 4mg group and three in the 16mg group, and its analytical handling is not reported.

The secondary outcome record offers limited additional statistical resolution. The early-relief comparison also has an interval spanning no difference; the remaining listed outcomes do not have analysis details in the information reported. Safety counts describe recorded events but do not establish comparative safety. Taken together, the record supports a careful account of observed counts and uncertainty, not a treatment recommendation or a broad claim about all patients, settings, or outcomes.

18. Why This Trial Matters Statistically

This trial illustrates why an observed difference in counts should be interpreted together with its uncertainty. The primary outcome count is higher in the 16mg group, but the recalculated interval extends across no difference and the unadjusted p-value is 0.312. Reporting only the direction of the observed counts would give an incomplete picture; the interval shows that the estimate is not precise enough to settle the direction or size of a population difference.

The record also shows how outcome definition shapes interpretation. Sustained relief requires both a symptom state of none or mild and maintenance of that state without rescue therapy through 48 hours. That is distinct from the separately listed early-relief outcome. Statistical conclusions apply to the endpoint that was defined and measured, rather than automatically extending to other symptom measures or time periods.

Planning illustrations demonstrate the relationship between the assumed effect size and required sample size. Under the stated assumptions, planning for a smaller fraction of the observed effect requires more participants per arm. This is useful for understanding design trade-offs, but the registry does not report the trial’s own sample-size justification. It would therefore be incorrect to use the illustrative figures to infer what the original investigators expected or whether the study met its planned target.

Finally, the record’s missing analysis details matter for reproducibility. The sponsor analysis is labeled as a risk ratio but lacks a method and p-value, while the primary endpoint has missing follow-up whose handling is not described. These gaps do not negate the posted results; they define the limits of what can be verified and interpreted. The statistical value of the record lies in distinguishing observed outcomes, uncertainty, and undocumented analytical choices.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several trial-specific limitations constrain interpretation. The registry notes that two participants in the dexamethasone 4mg group and three in the 16mg group did not complete 48-hour follow-up. It does not report how their outcomes were handled in the primary analysis, whether any imputation was used, or whether sensitivity analyses were conducted. The posted counts therefore cannot be fully evaluated for sensitivity to missing outcomes.

The sponsor analysis is labeled Risk Ratio (RR), but the reported value is 7 with a 95% confidence interval from -6 to 20. The analysis method and p-value are not reported, and the record does not explain the scale of the estimate or limits. This prevents direct reconstruction and makes comparison with the unadjusted risk-difference recalculation difficult. The record does not flag a discrepancy, but that does not supply the missing methodological detail.

Although five secondary outcomes are listed, detailed results are not reported for all of them in the analysis information. The registry also does not report a multiplicity adjustment, a hierarchy for secondary outcomes, or whether every planned analysis is represented. As a result, the secondary evidence cannot be assessed as a complete, prespecified family of comparisons.

The registry does not report the original sample-size justification, planned effect size, allocation ratio, randomization sequence procedure, or analysis population. It records quadruple masking but does not identify the masked roles or describe implementation. These omissions limit assessment of design and analysis choices. The adverse-event summaries are descriptive, with no comparative uncertainty estimates or causal assessments reported. Together, these limitations counsel against treating the posted estimates as more definitive than their methods and precision support.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Dexamethasone for Migraine - Dose Comparison — NCT04112823.
• Registry record last updated 2024-03-20; status last verified 2024-02.
• Results first posted 2024-03-20.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT04112823 is a completed, randomized, quadruple-masked, parallel phase 4 trial sponsored by Montefiore Medical Center. It compared intravenous dexamethasone 4mg with 16mg for acute migraine; the registry summary states that all patients also received metoclopramide. Enrollment was 209, with a start date of 2019-12-22 and primary completion on 2022-12-31.

The primary outcome was sustained headache relief over 48 hours, defined as none or mild headache without additional rescue therapy throughout follow-up. The posted counts were 35 of 102 in the 4mg group and 42 of 102 in the 16mg group. The unadjusted recalculation has an interval spanning no difference and a p-value of 0.312. The sponsor analysis is labeled Risk Ratio (RR), reports 7 with a 95% confidence interval from -6 to 20, and has no reported method or p-value.

The record notes missing 48-hour follow-up for two participants in the 4mg arm and three in the 16mg arm, without reporting the analysis handling. It lists five secondary outcomes, but does not report a multiplicity procedure or all secondary analysis details. The results are best read as observed counts with substantial uncertainty and limits to independent verification.