Childhood Absence Epilepsy Rx PK-PD-Pharmacogenetics Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Childhood Absence Epilepsy Rx PK-PD-Pharmacogenetics Study (NCT00088452), a randomized phase 3 study. The primary outcome is Number of Participants With Freedom From Treatment Failure at 16-20 Weeks of Double Blind Therapy.

2. Clinical Question

This is a comparison of initial treatment assignments in a parallel-group trial, not a comparison of every possible treatment sequence. The registry’s stated purpose was to determine the best initial treatment for childhood absence epilepsy. The outcome combines seizure control, tolerability, and treatment continuation: a participant could meet the failure definition for several different reasons. The registry record does not report how the individual reasons for failure were distributed, so the overall endpoint cannot establish which component chiefly explains the group pattern.

3. Trial Design

The registry identifies this as a randomized, triple-masked, parallel-group phase 3 study. Its enrollment is listed as 453. The three arms were ethosuximide, lamotrigine, and valproic acid. The sponsor was Children's Hospital Medical Center, Cincinnati. The recorded start was 2004-07, the primary completion was 2013-01, and the status is completed.

Random allocation is intended to make treatment groups comparable, on average, at the point of assignment. Masking is intended to reduce the influence of treatment knowledge on participants’ experience or on study procedures and assessments. The registry record identifies triple masking but does not report which roles were masked, how masking was maintained, or whether it was assessed. The parallel design means the arms represent concurrent assigned treatment groups rather than a crossover comparison.

The posted primary outcome counts were 81.0 of 154.0 for ethosuximide, 43.0 of 146.0 for lamotrigine, and 85.0 of 146.0 for valproic acid. These are outcome-specific denominators and counts; they should not be confused with the overall enrollment entry. The registry also lists attention deficit measured by the confidence index of the CPT-II and the K-CPT, and freedom from treatment failure at 12 months, as secondary outcomes. The participant counts for the attention outcome differ from those in the primary outcome record. Reasons for those differences, the analysis population definitions, and the trial’s original statistical plan are not reported in the registry record.

The arm descriptions state twice-daily dosing throughout study treatment. They also describe more than one formulation for each drug, with formulation choice dependent on weight and, for ethosuximide, ability to swallow. The available registry text does not contain a complete account of dosing or titration. It also does not report the original sample-size justification or the details of the randomization procedure.

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 Freedom From Treatment Failure at 16-20 Weeks of Double Blind Therapy, measured over First 16-20 weeks of double blind therapy.

The primary endpoint is the number of participants with freedom from treatment failure at 16-20 weeks of double-blind therapy. It is a binary outcome: each participant is counted as either meeting the freedom-from-failure definition or not meeting it. The registry labels the timeframe as the first 16-20 weeks of double-blind therapy.

Treatment failure was defined broadly. It included persistent absence seizures at week 16 or week 20, a generalized tonic-clonic seizure at any time, excessive drug-related systemic toxicity, a moderately severe possibly drug-related rash, pancreatitis, a body-mass-index increase of at least 3.0 from baseline, dose-limiting toxicity after a single downward dose modification, or withdrawal initiated by a parent or physician. Thus, the endpoint reflects more than seizure events alone: tolerability and continuation of assigned treatment also contribute.

A combined endpoint can capture whether a participant remains on treatment without one of the listed failures, which is relevant to an initial-treatment comparison. Its interpretation is nevertheless tied to the particular components and rules in the registry definition. The record does not report counts for each failure reason, how events were adjudicated, or how participants with incomplete follow-up were classified. Those details would help distinguish the clinical experiences represented by the overall count, but are not reported in the registry record.

7. Results Posted in the Registry

• Lamotrigine: 29.5% (43/146) versus 52.6% (81/154) on control; risk difference -23.1 percentage points (95% CI -34.0 to -12.3), risk ratio 0.56 (0.42–0.75); unadjusted two-proportion z-test p = <0.001.
• Valproic Acid: 58.2% (85/146) versus 52.6% (81/154) on control; risk difference 5.6 percentage points (95% CI -5.6 to 16.9), risk ratio 1.11 (0.90–1.36); unadjusted two-proportion z-test p = 0.328.

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 Attention Deficit as Measured by the Confidence Index of the CPT-II and the K-CPT

• 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:
  • Lamotrigine: 24.0% (25/104) versus 33.0% (35/106) on control; risk difference -9.0 percentage points (95% CI -21.1 to 3.2), risk ratio 0.73 (0.47–1.13); unadjusted two-proportion z-test p = 0.150.
  • Valproic Acid: 49.1% (52/106) versus 33.0% (35/106) on control; risk difference 16.0 percentage points (95% CI 3.0 to 29.1), risk ratio 1.49 (1.06–2.07); unadjusted two-proportion z-test p = 0.018.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lamotrigine and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Valproic Acid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Freedom From Treatment Failure at 12 Months of Double Blind Therapy

• 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:
  • Lamotrigine: 21.2% (31/146) versus 45.5% (70/154) on control; risk difference -24.2 percentage points (95% CI -34.5 to -13.9), risk ratio 0.47 (0.33–0.67); unadjusted two-proportion z-test p = <0.001.
  • Valproic Acid: 43.8% (64/146) versus 45.5% (70/154) on control; risk difference -1.6 percentage points (95% CI -12.9 to 9.6), risk ratio 0.96 (0.75–1.24); unadjusted two-proportion z-test p = 0.778.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Lamotrigine than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Valproic Acid and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address different aspects of the treatment experience: attention deficit measured by the confidence index of the CPT-II and the K-CPT, and freedom from treatment failure at 12 months. Across these outcomes, the observed group pattern is not uniformly the same for every drug and outcome. The secondary findings therefore add context rather than producing a single consistent extension of the primary comparison.

The attention outcome uses participant counts with denominators that differ from the primary endpoint denominators. The registry does not explain the difference, so it should not be assumed to reflect a particular exclusion, missing-data rule, or assessment process. The 12-month freedom-from-failure outcome is related to the primary endpoint by its treatment-failure construct, but its longer timeframe makes it a distinct outcome. Its results should not be read as simply repeating the earlier assessment.

There are multiple outcomes and pairwise comparisons in the registry. The posted recalculated secondary p-values are unadjusted, and the registry record does not report a multiplicity strategy. When many comparisons are considered, the chance of at least one apparently unusual result can increase. Secondary results are consequently more appropriately treated as supportive or exploratory unless a prespecified testing hierarchy or adjustment is documented. That hierarchy is not reported in the registry record.

The secondary findings do not erase or settle the primary-endpoint result. They answer related but nonidentical questions, use different outcome definitions or timeframes, and may involve different analysis denominators. Their value is in showing whether the broader pattern is consistent, while preserving uncertainty about why outcomes differ and how much weight to assign any individual secondary comparison.

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

• Number of Participants With Attention Deficit as Measured by the Confidence Index of the CPT-II and the K-CPT
• Number of Participants With Freedom From Treatment Failure at 12 Months of Double Blind Therapy

9. Statistical Interpretation

10. Statistical Methods Explained

The posted recalculations compare binary outcome proportions. For each arm, the outcome is a count of participants meeting the definition divided by that arm’s posted outcome denominator. A risk difference expresses the difference between those proportions on the probability scale. Its sign depends on the order of the comparison: a negative value for lamotrigine relative to ethosuximide indicates a lower observed proportion meeting the outcome in the lamotrigine arm, while a positive value indicates a higher proportion. This measure is directly interpretable as a difference in outcome probability, although the registry’s sponsor-reported analyses use odds ratios instead.

What does an odds ratio express?

An odds ratio compares the odds of an outcome between groups. Odds and probabilities are related but are not the same quantity, so an odds ratio should not be read as a risk difference or as a direct percentage-point change. An odds ratio above the null value of 1 indicates higher odds in the numerator group under the specified coding; a value below 1 indicates lower odds. The registry’s reported odds ratios must be read with attention to the group order and outcome coding. The record gives the odds-ratio estimates, confidence limits, methods, and p-values, but the discrepancy flag means these sponsor analyses take precedence over the independent recalculations.

How should a confidence interval be read?

A confidence interval gives a range of estimates compatible with the data and the method used, under repeated-sampling assumptions. It reflects sampling uncertainty; it is not a range containing every participant’s outcome, and it does not account automatically for bias, missing observations, or model misspecification. When an interval for a risk difference includes zero, the data are compatible with no difference as well as with effects on either side of zero. When it excludes zero, that is evidence against a no-difference value under the stated calculation, but it does not establish that the difference is clinically important or free of bias.

What do the p-values contribute?

A p-value describes how unusual data at least as inconsistent with the null model would be if that model and the analysis assumptions held. It is not the probability that the null hypothesis is true, nor is it the probability that a result occurred by chance. A small p-value does not quantify the effect size, and a larger p-value does not prove equivalence. The posted recalculated p-values are unadjusted. They therefore do not account for the multiplicity of examining more than one contrast and more than one endpoint.

Why can the analysis method matter?

The sponsor reports Chi-squared analyses for the primary outcome and attention outcome, and Fisher Exact analyses for the 12-month outcome. These are methods for analyzing categorical data. A Chi-squared test uses an approximation based on the observed group counts; Fisher Exact evaluates the data under a fixed-margin framework and can be useful when counts are sparse. The registry record does not report the sponsor’s rationale for selecting methods by outcome, nor does it provide enough detail to reconstruct all analysis choices.

What is the role of recalculation?

The recalculated risk differences are simple, unadjusted comparisons from the posted arm-level counts. They do not incorporate participant-level information, covariate adjustment, stratification, or any additional analytic choices unless those are encoded in the summary data, which is not reported. They offer a transparent view of the count pattern, but are not a substitute for the sponsor’s analysis. The record explicitly flags a discrepancy, so the sponsor’s own analysis takes precedence. The original statistical analysis plan, including planned estimands, handling of protocol deviations, and any prespecified adjustment, is not reported in the registry record.

Because the primary outcome is binary, over-dispersion—a concept relevant to some count or rate models—is not the central issue for these simple comparisons. More generally, over-dispersion occurs when count data vary more than a model assumes, which can make standard errors too small if ignored. That general concern should not be attributed to this analysis: the registry describes participant counts and categorical comparisons, not a count-rate model. The key interpretive limitations are instead the outcome definition, uncertainty, analysis discrepancy, and unreported handling of missing data and multiplicity.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a group difference. The recalculated primary risk difference comparing lamotrigine with ethosuximide is -0.232, with a 95% confidence interval from -0.340 to -0.123. The interval is entirely below zero, indicating that the unadjusted estimate is separated from no difference under this calculation. Its width also shows that the data remain compatible with a range of negative differences rather than a single exact effect.

For valproic acid relative to ethosuximide, the risk difference is 0.056, with a 95% confidence interval from -0.056 to 0.169. Because this interval crosses zero, the data are compatible with no difference as well as with a lower or higher outcome proportion for valproic acid. The interval is not evidence that the treatments are equivalent; an equivalence conclusion requires a prespecified margin and suitable analysis, which are not reported in the registry record.

Confidence intervals address sampling uncertainty under the calculation’s assumptions. They do not reflect all possible sources of uncertainty, including bias from missing outcomes, deviations from the intended analysis, or the discrepancy between recalculated and sponsor-reported analyses. No adjusted confidence intervals for the primary outcome are reported in the registry record. The sponsor’s own odds-ratio intervals are reported for its pairwise analyses, but those use a different effect measure and comparison coding, so they should not be substituted directly for the risk-difference intervals.

Precision should be considered alongside the endpoint definition and the number of analyses. An interval can be statistically narrow yet concern a composite outcome whose components have different meanings. Conversely, an interval that includes the null may still encompass effects that could matter in context. The registry record does not report a prespecified threshold for clinical importance, so the confidence intervals describe statistical uncertainty without establishing what magnitude would be clinically important.

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 expressed as participants per arm for the binary outcomes in this trial, not as total events. The sample-size 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. The original design assumptions and the trial’s own sample-size justification are not reported in the registry record.

The 80% power column gives the per-arm planning size under which the stated assumed effect would be detected by the specified test in 80% of repeated studies, if the planning assumptions hold. The 90% power column describes the corresponding planning size for a higher chance of detecting that assumed effect. These are prospective planning illustrations derived from the observed effect, not observed power for the completed trial.

Rows that plan for 75% or 50% of the observed effect assume a smaller difference to detect than the row using 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same assumptions. This explains why the listed planning sizes generally rise as the assumed effect is reduced. When the observed effect is near zero, the illustrative requirements can become very large; such figures should not be interpreted as a recommendation for a future study without a clinically justified target effect and a complete design.

The curve and table are planning aids, not evidence about the trial’s original target enrollment or whether the completed study had adequate power. Their estimates rely on the observed effect, which is uncertain, and on simplified assumptions such as equal allocation and a normal approximation. They do not account for unreported design features, losses to follow-up, multiplicity adjustment, or the discrepancy between sponsor and recalculated analyses. These figures therefore illustrate how sample size changes with the target effect and desired power rather than reconstructing the trial’s original planning process.

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 = 0.526; treatment proportion p₁ = 0.295; average p̄ = 0.410.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6956 = 1.3634.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6761 = 0.5690.
4. n = (1.3634 + 0.5690)² / (-0.2315)² = 69.7, rounded up to 70 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 <- 0.525974025974026                          # control proportion
p1 <- 0.294520547945205                          # 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(88452)
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 = 70 (80% power), 93 (90% power)
 75% of observed effect: n per arm = 128 (80% power), 170 (90% power)
 50% of observed effect: n per arm = 291 (80% power), 389 (90% power)
power.prop.test: 69.7 
Simulated power at n = 70 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. Analyses Reported by the Sponsor

The sponsor’s posted primary-outcome analyses report odds ratios from Chi-squared tests. The analysis comparing ethosuximide with lamotrigine reports an odds ratio of 2.66, a 95% confidence interval from 1.65 to 4.28, and p < 0.001. The comparison of lamotrigine with valproic acid reports an odds ratio of 3.34, a 95% confidence interval from 2.06 to 5.42, and p < 0.001. These are the sponsor’s own analyses and use odds ratios rather than the recalculated risk differences.

The recalculations use posted arm-level counts to estimate unadjusted risk differences against ethosuximide. Their contrast set and effect measure do not reproduce every sponsor-reported comparison. The registry record flags a discrepancy between the sponsor results and the recalculated results. Under that circumstance, the sponsor’s own analysis takes precedence; the recalculated values should be treated as supplementary descriptions of the posted counts, not as corrections to or replacements for the sponsor’s findings.

The registry does not report enough detail to determine the source of the discrepancy or to fully reconcile the analyses. In particular, the original statistical analysis plan, participant-level data, and complete coding and modeling details are not reported in the registry record. The sponsor results should therefore be quoted as registered, while keeping clear that odds ratios and risk differences are different measures and that the pairwise comparisons do not all use the same reference group.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and secondary outcomes, with multiple pairwise analyses. The record does not report a family-wise error strategy, a false-discovery procedure, a prespecified testing hierarchy, or another multiplicity adjustment. The posted recalculated p-values are unadjusted. When several hypotheses are tested, interpreting each p-value as if it were the only planned test can overstate the strength of evidence. This concern is especially relevant to secondary outcomes, which are generally less decisive when their role and testing sequence are not specified.

Multiplicity is not the same as bias, and it does not automatically invalidate a result. It changes how much evidential weight should be placed on a collection of tests. The sponsor’s reported primary and secondary analyses should be interpreted according to their own methods, but the registry record does not establish whether the reported testing plan controlled error across outcomes or comparisons. The original protocol and statistical analysis plan are not reported in the registry record.

Missing-data methods are also not reported. The primary outcome denominators differ by arm, and the attention outcome denominators differ from the primary outcome denominators. These registry entries alone do not show why observations are absent from a particular analysis, whether any outcome data were missing, or how any missing values were handled. The registry record does not report imputation, complete-case rules, sensitivity analyses, or reasons for exclusion.

The analysis populations are not fully described. The registry record does not say whether the analyses followed intention-to-treat, per-protocol, or another population definition, or how treatment discontinuation and protocol deviations were handled beyond the treatment-failure definition itself. It also does not report interim analyses or stopping rules. These omissions limit independent assessment of the analysis process; they should not be filled by assumptions about common trial practice.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: generalized tonic clonic seizure (1.3%), acting out (0.7%), enteritis (0.7%), prolonged absence seizure (0.7%), pneumonia, diarrhea, vomiting (0.6%).

The serious adverse event summary lists 4 affected participants among 155 at risk for ethosuximide, 2 among 149 for lamotrigine, and 2 among 147 for valproic acid. The registry reports zero deaths in each group. The other adverse-event counts are 103 among 155, 78 among 149, and 100 among 147, respectively. These are registry counts with their own at-risk denominators, which differ from the primary efficacy denominators.

The registry also identifies serious-event terms and percentages, including Generalized tonic clonic seizure at 1.3%, Acting Out at 0.7%, Enteritis at 0.7%, Prolonged Absence Seizure at 0.7%, Pneumonia, diarrhea, vomiting at 0.6%, and Non-epileptic movements at 0.6%. These terms describe events recorded in the safety summary; they do not by themselves establish that a study drug caused an event. The posted figures do not provide participant-level timing, exposure duration, recurrence, severity detail beyond the serious-event designation, or a causal assessment for each event.

Safety counts should be interpreted alongside the way events were collected and the time each participant was observed. Those details are not reported in the registry record. The counts are descriptive and should not be treated as a complete comparison of all possible risks.

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

The registry results describe how the three assigned groups compared on a defined measure of freedom from treatment failure and on the listed secondary and safety outcomes. The primary outcome combines persistent absence seizures, other specified clinical events, toxicity, and treatment withdrawal. It is therefore a measure of remaining free of a range of treatment failures, not a seizure-only measure or a direct assessment of every aspect of treatment experience.

The recalculated primary risk differences suggest a different observed pattern for lamotrigine relative to ethosuximide than for valproic acid relative to ethosuximide. The confidence intervals also convey different levels of uncertainty about those contrasts. These recalculations are unadjusted and the record flags a discrepancy with the sponsor’s analysis, which takes precedence. The sponsor’s odds ratios should be interpreted in their own metric and with attention to the group order.

The findings do not establish that a drug works or does not work, and they do not provide medical advice or a treatment recommendation. Nor do they establish that the observed group pattern will apply to every child with absence epilepsy. The registry record does not report sufficient details about participant characteristics, complete analysis populations, missing-data handling, or clinically meaningful thresholds to support those broader conclusions.

A statistically detectable difference is not automatically a clinically important difference. A result that does not meet a conventional statistical threshold is not proof of equivalence or absence of an effect. Clinical importance depends on the size and nature of the effect, the components of the endpoint, the balance of benefits and harms, and the population to which the evidence applies. The registry record does not report a prespecified threshold for interpreting clinical importance.

The most defensible reading is therefore bounded: these are comparisons within a randomized, triple-masked, parallel-group trial with the registered outcome definitions and available summary results. The analysis is informative about the registered comparisons, while uncertainty about the discrepancy, endpoint components, multiplicity, missing data, and generalizability remains.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of effect measure matters. The registry’s sponsor analyses report odds ratios, while the recalculations express differences as risk differences. These measures answer related but distinct questions and have different scales. A reader should not compare their numerical magnitudes as if they were interchangeable, and the risk difference’s direction depends on which arm is used as the reference.

The primary endpoint also shows how a composite outcome can simplify an analysis while joining events that have different meanings. Persistent seizures, toxicity, a possible drug-related rash, pancreatitis, a change in body-mass index, dose-limiting toxicity, and withdrawal all count toward treatment failure under the registry definition. An overall count can summarize whether a participant remained free of the specified failures, but it does not show which component drives a difference unless component-level results are reported.

The record further demonstrates the importance of separating the sponsor’s analysis from simple recalculation. Arm-level counts allow a transparent unadjusted comparison, but they do not reproduce all design and analysis choices. When the registry flags a discrepancy, the sponsor’s own analysis takes precedence. This distinction protects against treating a summary-statistic reconstruction as an authoritative reanalysis.

Finally, uncertainty is not captured by a p-value alone. Confidence intervals show the range of effect sizes compatible with the data and help distinguish a precise estimate from a result that remains compatible with materially different directions or magnitudes. Planning illustrations can show how a target effect and desired power affect required sample size, but they do not reveal the trial’s original justification or observed power. These are broadly useful lessons for interpreting registered clinical-trial results.

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 details needed for a fuller interpretation are not reported in the registry record. The participant profile and eligibility criteria are not presented in the available record, limiting assessment of how closely the enrolled population represents other clinical settings. The arm descriptions indicate twice-daily treatment and some formulation choices, but the available dosing and titration text is incomplete. The full treatment regimens therefore cannot be reconstructed from this record.

The primary endpoint combines clinically different failure reasons, but component counts are not reported. This prevents assessment of whether the overall pattern was driven by seizure persistence, adverse effects, withdrawal, or another listed component. The record also does not report adjudication procedures for events, analysis-population definitions, or how treatment discontinuation and protocol deviations were handled.

The discrepancy between sponsor analyses and recalculated results limits direct reconciliation. Participant-level data and the complete statistical analysis plan are not reported, so the source of the discrepancy cannot be established from the registry record. Multiplicity adjustment, missing-data handling, and interim analyses are also not reported. The secondary outcome denominators differ from the primary outcome denominators, but the reason is not recorded.

These limitations concern the information available in the registry record; they do not establish that the trial lacked procedures or analyses that were not posted. They restrict what can be independently verified from the registered summary and counsel against extending the estimates beyond the specific outcomes and comparisons reported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Childhood Absence Epilepsy Rx PK-PD-Pharmacogenetics Study — NCT00088452.
• Registry record last updated 2020-10-14; status last verified 2017-02.
• Results first posted 2020-10-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, triple-masked, parallel-group phase 3 study of ethosuximide, lamotrigine, and valproic acid for childhood absence epilepsy. Enrollment is listed as 453, with start in 2004-07 and primary completion in 2013-01. The primary outcome was freedom from treatment failure during the first 16-20 weeks of double-blind therapy.

Primary outcome counts and recalculated unadjusted risk differences are posted alongside sponsor-reported odds-ratio analyses. The record flags a discrepancy, so the sponsor’s own analysis takes precedence over recalculations. Secondary outcomes concern attention deficit and freedom from treatment failure at 12 months. Safety counts include serious and other adverse events and zero deaths in each group.

The registry does not report the original sample-size justification, complete analysis plan, multiplicity strategy, missing-data methods, or full analysis-population definitions. Accordingly, the results support interpretation of the registered comparisons, but not unsupported conclusions about unreported design or analysis choices.