Established Status Epilepticus Treatment Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Established Status Epilepticus Treatment Trial (NCT01960075), a randomized phase 3 study. The primary outcome is Number of Participants With Clinical Cessation of Status Epilepticus - Intention to Treat.

2. Clinical Question

3. Trial Design

The Established Status Epilepticus Treatment Trial (NCT01960075) was a phase 3, randomized, triple-masked, parallel-group comparative-effectiveness study sponsored by the University of Virginia. Its official title describes a multicenter study in the emergency department. The three active treatment groups received fosphenytoin, valproic acid, or levetiracetam. No placebo group is listed.

The registry record gives enrollment as 478. The primary endpoint result does not use that enrollment total as its analysis denominator: its population note says that the total of 384 is from the first 400 patients and excludes 16 re-enrollers. It also states that the first 400 patients were used because of a prespecified stopping rule and that the trial stopped for futility. The original rationale and operating details for that rule are not reported in the registry record.

The primary endpoint was clinical cessation of status epilepticus within 60 minutes after the start of study drug infusion. The registry record also lists secondary outcomes involving intensive care admission, ICU stay, time to seizure termination among participants with treatment success, seizure cessation within 20 minutes among those participants, and hospital stay. Numerical results are posted for ICU admission and seizure cessation within 20 minutes. Results for the other listed secondary outcomes are not reported in the registry record.

The registry record gives the trial start as 2015-10 and primary completion as 2019-02, with status completed. It does not report the original sample-size justification, the intended statistical analysis plan, or details of masking procedures. The population's age range is described as older than 2 years in the trial objective; further age-specific findings 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

Analysis population for the primary outcome, as defined in the registry: The difference from Participant Flow is because the total of 384 is from the first 400 patients and excludes 16 re-enrollers in the study. The first 400 patients were used because of the prespecified stopping rule and the trial stopped for futility.

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: The difference from Participant Flow is because the total of 384 is from the first 400 patients and excludes 16 re-enrollers in the study, and the first 400 patients were used because of the prespecified stopping rule and the trial stopped for futility.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Clinical Cessation of Status Epilepticus - Intention to Treat, measured over Within 60 minutes after the start of study drug infusion.

The primary endpoint counts participants who experienced clinical cessation of status epilepticus within 60 minutes after study drug infusion began. The stated definition requires both the absence of clinically apparent seizures and improving consciousness at 1 hour, without other anticonvulsant medications. This is a binary outcome for each participant: the registry reports how many met the endpoint in each treatment group, together with the group totals.

This endpoint focuses on a clinically observable status—seizures have stopped and consciousness is improving—rather than on a laboratory measure or a symptom scale. Its fixed assessment window makes the outcome comparable across the three treatment groups. The endpoint description also makes clear that seizure cessation alone was not sufficient under the stated definition if consciousness was not improving, and that use of other anticonvulsant medications was excluded from the success definition.

The objective named in the registry record was to determine the most effective and/or least effective treatment among the three active options. An intention-to-treat label is attached to the primary outcome, but the population note narrows the reported result: it identifies 384 participants drawn from the first 400 patients and excludes 16 re-enrollers. Thus, the label should be read alongside that stated analysis population rather than assumed to mean that all 478 enrolled participants contributed to this endpoint result.

The endpoint is a count of participants with an event, not a measure of how long seizures lasted or how quickly they stopped. Time to termination and seizure cessation within 20 minutes appear among the secondary outcomes. Their posted results therefore address related but distinct aspects of seizure control.

7. Results Posted in the Registry

• Valproic Acid: 46.3% (56/121) versus 44.9% (53/118) on control; risk difference 1.4 percentage points (95% CI -11.3 to 14.0), risk ratio 1.03 (0.78–1.36); unadjusted two-proportion z-test p = 0.832.
• Levetiracetam: 46.9% (68/145) versus 44.9% (53/118) on control; risk difference 2.0 percentage points (95% CI -10.1 to 14.1), risk ratio 1.04 (0.80–1.36); unadjusted two-proportion z-test p = 0.748.

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 Participants With Admission to Intensive Care Unit

• 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:
  • Valproic Acid: 58.7% (71/121) versus 59.3% (70/118) on control; risk difference -0.6 percentage points (95% CI -13.1 to 11.8), risk ratio 0.99 (0.80–1.22); unadjusted two-proportion z-test p = 0.919.
  • Levetiracetam: 60.0% (87/145) versus 59.3% (70/118) on control; risk difference 0.7 percentage points (95% CI -11.2 to 12.6), risk ratio 1.01 (0.83–1.24); unadjusted two-proportion z-test p = 0.911.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Valproic Acid 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 Levetiracetam and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Seizure Cessation Within 20 Minutes for Patients With Treatment Success

• 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:
  • Valproic Acid: 78.2% (43/55) versus 81.1% (43/53) on control; risk difference -3.0 percentage points (95% CI -18.1 to 12.2), risk ratio 0.96 (0.80–1.17); unadjusted two-proportion z-test p = 0.704.
  • Levetiracetam: 77.9% (53/68) versus 81.1% (43/53) on control; risk difference -3.2 percentage points (95% CI -17.6 to 11.2), risk ratio 0.96 (0.80–1.15); unadjusted two-proportion z-test p = 0.667.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Valproic Acid 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 Levetiracetam and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes give additional perspectives on care after study drug infusion, but they do not replace the primary measure of clinical cessation within 60 minutes. The posted ICU-admission counts are broadly similar across the three groups, and the unadjusted risk-difference intervals for each comparison with fosphenytoin cross zero. For seizure cessation within 20 minutes, the counts concern only participants classified as having treatment success; that restricted population differs from the primary endpoint population. The corresponding unadjusted intervals also cross zero.

These patterns are consistent with the primary result in one limited sense: the posted comparisons do not show a clear separation between the active groups. They should not be treated as repeated versions of the same endpoint. ICU admission describes a care setting, while early seizure cessation concerns timing among participants with treatment success. The listed outcomes of ICU length of stay, time from infusion to seizure termination among successes, and hospital length of stay have no numerical results reported in the registry record.

Secondary findings generally carry less confirmatory weight when several outcomes and comparisons are examined without a reported multiplicity plan. The registry record does not report an adjustment for multiple testing, a hierarchy for interpreting secondary outcomes, or a full analysis plan. Unadjusted secondary estimates can be useful descriptively, but isolated apparent differences should not be treated as definitive evidence.

The reported information therefore supports a cautious overall reading: selected secondary counts do not supply a clear contrasting pattern that resolves the uncertainty in the primary comparisons. They add context, while their distinct definitions, restricted populations, and unreported analyses limit how strongly they can reinforce or challenge the primary finding.

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

• Number of Participants With Admission to Intensive Care Unit
• Length of ICU Stay
• Minutes From Start of Trial Drug Infusion to Termination of Seizures for Patients With Treatment Success
• Number of Participants With Seizure Cessation Within 20 Minutes for Patients With Treatment Success
• Length of Hospital Stay

9. Statistical Interpretation

10. Statistical Methods Explained

Binary endpoint and group counts. The primary outcome is binary because each participant either met the definition of clinical cessation within the specified window or did not. The posted count is paired with the number of participants in the group. The registry lists 53 of 118 for fosphenytoin, 56 of 121 for valproic acid, and 68 of 145 for levetiracetam. These counts are the basis for the unadjusted comparisons; they do not, by themselves, account for covariates or other design features.

Risk difference. A risk difference compares the proportion with the event in one group with the proportion in another. A value on the positive side indicates a higher event proportion in the first-named treatment group under the comparison's direction; a value on the negative side indicates a lower proportion. Zero represents no difference in the event proportions. The posted comparisons use fosphenytoin as the reference group, and both primary-outcome confidence intervals cross zero. The registry record does not describe a covariate-adjusted model for these comparisons.

Confidence interval. In general, a confidence interval describes the range of effect estimates that are reasonably compatible with the observed data under the method used. It is not a guarantee that the true effect lies inside a particular interval, and it does not assign a probability to a treatment being better. For the posted risk differences, intervals crossing zero indicate that the data do not rule out no difference under the interval procedure. The confidence level and the full interval-construction method are not reported in the registry record, so the interval should not be labeled with an unreported confidence level.

Unadjusted p-values. A p-value measures how unusual data at least as discrepant as those observed would be under a specified null model. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. The primary comparisons list unadjusted p-values of 0.832 for valproic acid versus fosphenytoin and 0.748 for levetiracetam versus fosphenytoin. The registry record does not describe the test used to obtain these p-values or a multiplicity adjustment. They should therefore be read as unadjusted comparison results, not as a complete account of the analysis plan.

Intention-to-treat and the analysis population. Intention-to-treat generally means analyzing participants according to their randomized assignment, regardless of treatment received or adherence, subject to the stated analysis population and available outcome data. Here, the primary endpoint carries that label, while the accompanying note says the result uses the first 400 patients and a total of 384, excluding 16 re-enrollers. The registry record does not explain how missing endpoint data were handled, whether all randomized participants in that subset had an observed endpoint, or whether additional analysis populations were used. These details are important when interpreting what the intention-to-treat label covers in practice.

Stopping for futility. In general, a futility rule is used to identify circumstances in which continuing a study is judged unlikely to achieve its objective under the specified plan. The registry record says a prespecified stopping rule led to the use of the first 400 patients and says the trial stopped for futility. However, the boundary, interim-analysis schedule, and decision criteria are not reported in the registry record. It is therefore not possible to reconstruct the stopping procedure or infer its exact statistical properties from the posted outcome counts.

Secondary outcomes and multiplicity. A trial that examines multiple treatments and outcomes can generate multiple statistical comparisons. If each comparison is considered separately without adjustment, the chance of at least one apparently notable result can increase. This is a general statistical concern, not evidence that any particular posted finding is false. The secondary comparisons are unadjusted, and no multiplicity strategy is reported in the registry record. The results are best treated as additional descriptive evidence rather than as a separate confirmatory test of the primary question.

Count outcomes and event timing. ICU admission and seizure cessation within 20 minutes are also presented as participant counts. The time-to-seizure-termination outcome is listed for participants with treatment success, but numerical results for that outcome are not reported in the registry record. Counts and timing answer different questions: a count identifies how many participants met a criterion, while a time measure describes when an event occurred. The registry record does not report the analysis method planned for the listed timing outcomes.

Limits of reconstruction. The registry record contains outcome counts and unadjusted comparison summaries, but it does not report the original statistical analysis plan, model specifications, missing-data procedures, or subgroup analysis plan. Those omissions prevent a fuller assessment of how the analyses were prespecified and implemented. General explanations of risk differences, confidence intervals, p-values, intention-to-treat analysis, futility, and multiplicity clarify the posted quantities; they do not fill in those unreported trial-specific methods.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an effect estimate. The primary risk-difference confidence intervals extend across zero for both comparisons with fosphenytoin. In practical terms, the posted intervals do not isolate a difference in one direction: they include no difference and allow estimates on either side. That breadth means the observed data do not pin down the comparative effect precisely.

The event counts provide context for that uncertainty. The primary outcome was recorded for 118 participants in the fosphenytoin group, 121 in the valproic acid group, and 145 in the levetiracetam group. With these group totals and the posted event counts, the comparison estimates remain uncertain; the registry's interval estimates make that uncertainty explicit. The record does not report a confidence level or the interval method, so neither should be assumed.

A confidence interval is not a range of outcomes for individual participants, and it does not mean that every value inside it is equally plausible. It summarizes uncertainty in an estimated group contrast under a statistical procedure. An interval crossing zero does not prove that the true difference is zero; it indicates that zero is among the values not excluded by the interval.

The secondary risk-difference intervals for ICU admission and seizure cessation within 20 minutes also cross zero. Those estimates have their own denominators and answer separate questions, so their precision cannot be inferred from the primary endpoint alone. The registry record does not provide numerical precision estimates for every listed secondary outcome.

Most importantly, statistical uncertainty and clinical importance are distinct. A relatively broad interval can leave open effects that might matter, while a narrow interval can be more informative about which effects remain compatible with the data. No threshold for a clinically important difference is reported in the registry record, so the intervals cannot be classified against such a threshold.

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 illustrations based on the observed treatment effect, not the trial's original design calculations. The original sample-size assumptions and justification are not reported in the registry record. For the binary outcomes shown, the figures are participants per arm, not total participants or total events. The planning method assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers an effect equal to the stated fraction of the observed effect.

The 80% power column gives the estimated number of participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect is real and the statistical model's assumptions hold. The 90% power column uses the same idea with a higher chance of detecting that effect, and therefore calls for a larger planned sample in the displayed calculations. For example, the levetiracetam-versus-fosphenytoin primary comparison gives 9,929 participants per arm for 80% power and 13,292 participants per arm for 90% power when planning for 100% of the observed effect.

Rows planning for 75% or 50% of the observed effect consider smaller effects than the full observed estimate. Smaller effects are harder to distinguish from random variation, so they require more participants under the stated assumptions. These calculations use the observed effect as a starting point; they do not establish that the observed effect is stable, clinically important, or the effect a future study should expect.

Power is a property of a planned study under specified assumptions. The figures are not observed power for this completed trial and do not show the probability that the trial's conclusion is correct. They are planning illustrations only. The registry record does not report whether the original design used these assumptions or a different approach.

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 = 0.449; treatment proportion p₁ = 0.463; average p̄ = 0.456.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7044 = 1.3805.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7043 = 0.5927.
4. n = (1.3805 + 0.5927)² / (0.0137)² = 20,875.6, rounded up to 20,876 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 <- 0.449152542372881                          # control proportion
p1 <- 0.462809917355372                          # 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(1960075)
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 = 20,876 (80% power), 27,947 (90% power)
 75% of observed effect: n per arm = 37,091 (80% power), 49,653 (90% power)
 50% of observed effect: n per arm = 83,401 (80% power), 111,650 (90% power)
power.prop.test: 20875.6 
Simulated power at n = 20,876 per arm: 0.802 (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. Multiplicity, Missing Data and Analysis Populations

The trial compares three active treatments and includes multiple outcomes. This creates a multiplicity issue: if many comparisons are assessed independently, some results may appear statistically notable by chance even when there are no corresponding underlying differences. A prespecified strategy can address that issue by defining which outcomes and comparisons are confirmatory and how the error rate is controlled. Such a strategy is not reported in the registry record.

The posted comparison p-values are unadjusted. The record does not report whether the primary comparison family was treated as a single overall test, whether pairwise comparisons were planned in advance, or whether any adjustment was applied in the sponsor's analysis. It also does not report a hierarchy linking primary and secondary outcomes. As a result, the unadjusted p-values should not be interpreted as if they accounted for all comparisons made in the trial.

Missing-data handling is also not reported in the registry record. The primary endpoint is labeled intention-to-treat, but the record does not describe the number of missing primary outcomes, how missing outcomes were classified or imputed, or whether sensitivity analyses assessed the impact of missingness. The population note states that the reported total of 384 came from the first 400 patients and excludes 16 re-enrollers. It does not explain any additional participant-level exclusions or the reason all other enrollment records are not part of that endpoint total.

Analysis-population details are limited. The intention-to-treat label is present for the primary result, but per-protocol or safety analysis populations are not described as formal analysis sets. The adverse-event denominators differ from the primary endpoint group totals, and the registry gives at-risk counts for those safety summaries. It does not explain the relationship between those denominators and the primary endpoint population.

Finally, the registry says the trial stopped for futility under a prespecified stopping rule, but the timing and statistical details are not reported. The interim-analysis plan, stopping boundary, and any adjustments to inference after stopping are therefore unknown. These absences limit independent evaluation of the complete statistical plan; they do not establish that appropriate procedures were or were not used.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: convulsion (20.0%), respiratory depression (12.0%), depressed level of consciousness (10.0%), hypotension (5.6%), respiratory failure (3.2%).

The safety summaries report serious adverse events, other adverse events, and deaths with group-specific numbers at risk. Serious adverse events were reported for 57 of 125 participants in the fosphenytoin group, 46 of 125 in the valproic acid group, and 64 of 150 in the levetiracetam group. Other adverse events were reported for 28 of 125, 22 of 125, and 25 of 150, respectively. Deaths were recorded for 3, 2, and 7 participants, respectively. These are counts as posted; they should not be interpreted as evidence that treatment caused an event or death.

The registry lists serious adverse-event terms including convulsion, respiratory depression, depressed level of consciousness, hypotension, respiratory failure, and encephalopathy, with the percentages 20.0%, 12.0%, 10.0%, 5.6%, 3.2%, and 2.7%, respectively. The registry record does not give further detail about the denominator or attribution for these listed terms in the summary. Such percentages and counts do not establish comparative safety without the relevant analysis, context, and uncertainty estimates.

The at-risk totals in the safety summary are not the same as the primary endpoint group totals. No statistical comparison of adverse events or deaths is reported in the registry record. These summaries describe recorded events and should be read as safety information, not as a causal or definitive ranking of the treatments.

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

The primary result describes clinical cessation of status epilepticus within 60 minutes after infusion began, using the registry's stated criteria. The event counts are 53 of 118 for fosphenytoin, 56 of 121 for valproic acid, and 68 of 145 for levetiracetam. The unadjusted pairwise comparisons with fosphenytoin have p-values of 0.832 and 0.748, and the posted confidence intervals cross zero. Together, these summaries indicate that the data do not clearly distinguish the active groups on this endpoint.

That interpretation is narrower than saying that the treatments are the same. Demonstrating equivalence or noninferiority requires a suitable design, a prespecified margin, and an analysis targeted to that question. No equivalence or noninferiority margin is reported in the registry record. The results also do not show that a clinically meaningful difference is impossible; the confidence intervals reflect remaining uncertainty.

The registry record reports that the trial stopped for futility after a prespecified stopping rule and that the primary endpoint result uses the first 400 patients, with a total of 384 after excluding 16 re-enrollers. This trial context matters when reading the posted outcome results. The details needed to reconstruct the stopping process or evaluate all analysis decisions are not reported in the registry record.

Nor do these results establish how the treatments compare for every outcome of interest. Secondary outcomes address ICU admission, hospital and ICU stays, and seizure timing, but numerical results are posted for only selected outcomes. The posted secondary comparisons are unadjusted, and a multiplicity strategy is not reported. Safety counts describe recorded events but do not by themselves establish causation or comparative risk.

The results are evidence from one randomized, triple-masked, parallel-group trial in patients older than 2 years with benzodiazepine-refractory status epilepticus. They are not a treatment recommendation, a guarantee about an individual participant's outcome, or proof that one treatment is better or worse. Their meaning depends on the endpoint definition, the stated analysis population, the uncertainty around comparisons, and the statistical details that the registry record does not report.

17. Why This Trial Matters Statistically

This trial raises a central statistical challenge in comparative effectiveness research: a study can compare several active treatments without producing a clear ranking. The primary endpoint uses a clinically observable binary outcome, and the posted counts show clinical cessation in every group. Yet the unadjusted comparisons with fosphenytoin have confidence intervals that cross zero. The distinction between observing different counts and demonstrating a reliably estimated treatment contrast is essential to sound interpretation.

The trial also illustrates why the analysis population and trial conduct matter alongside the headline enrollment. The record gives enrollment as 478, but the primary outcome note specifies a total of 384 from the first 400 patients and excludes 16 re-enrollers. It says a prespecified stopping rule led to use of those first 400 and that the trial stopped for futility. Readers need those details to understand which participants contributed to the posted primary result, while the absent stopping-rule details limit independent statistical reconstruction.

Several related outcomes can help describe a treatment comparison, but they are not interchangeable. ICU admission, rapid seizure cessation among treatment successes, time to seizure termination, and length of stay address different questions and may involve different analysis populations. The registry record's limited numerical reporting for these outcomes, together with the absence of a reported multiplicity plan, illustrates why secondary findings need careful qualification.

Finally, planning calculations derived from observed effects can show how sample-size requirements change when the target effect changes. They are not substitutes for the original design justification and are not evidence of the completed trial's power. Keeping those distinctions clear helps prevent uncertain estimates, stopping decisions, secondary comparisons, and planning illustrations from being overstated.

18. Limitations

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

The registry record leaves important trial-specific statistical details unreported. It does not provide the original sample-size justification, full analysis plan, model specifications, missing-data procedures, or confidence-interval construction method. The confidence level for the posted intervals is not reported. These gaps limit assessment of how the comparisons were planned and carried out.

The primary outcome population requires particular care. The endpoint is labeled intention-to-treat, but the population note says that the total of 384 is from the first 400 patients and excludes 16 re-enrollers. The overall enrollment is 478. The record does not explain in detail how participants outside the stated primary endpoint set were handled or whether missing endpoint information affected the counts.

The trial stopped for futility under a prespecified rule, but the registry record does not report interim-analysis timing, stopping boundaries, or the statistical adjustment, if any, associated with that decision. Without those details, the stopping process and its influence on the interpretation cannot be reconstructed from the posted summary.

Several secondary outcomes are listed, but numerical results are not reported for ICU length of stay, time to seizure termination among participants with treatment success, or hospital length of stay. Results are posted for ICU admission and seizure cessation within 20 minutes, but their comparisons are unadjusted and no multiplicity strategy is reported. The secondary outcomes also differ in their populations and definitions.

The safety summary presents counts and at-risk totals, but does not provide comparative statistical analyses or enough context to infer causation. The record's stated population is patients older than 2 years, while age-specific effectiveness and safety findings are not reported. These limitations constrain the scope and precision of conclusions that can be drawn from the registry summaries.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Established Status Epilepticus Treatment Trial — NCT01960075.
• Registry record last updated 2021-06-14; status last verified 2021-05.
• Results first posted 2020-02-28.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01960075, the Established Status Epilepticus Treatment Trial, was a completed phase 3, randomized, triple-masked, parallel-group study sponsored by the University of Virginia. It compared intravenous fosphenytoin, valproic acid, and levetiracetam in patients older than 2 years with benzodiazepine-refractory status epilepticus. The registry reports enrollment of 478 and identifies the primary endpoint as clinical cessation within 60 minutes after infusion began.

The primary outcome counts were 53 of 118 for fosphenytoin, 56 of 121 for valproic acid, and 68 of 145 for levetiracetam. The primary endpoint note states that its total of 384 came from the first 400 patients and excludes 16 re-enrollers; it also says the trial stopped for futility under a prespecified stopping rule. The posted unadjusted comparisons do not clearly distinguish the active groups. Further details on the statistical plan, missing data, multiplicity, and stopping procedures are not reported in the registry record.