Levetiracetam Versus Topiramate as Adjunctive Therapy to Evaluate Efficacy and Safety in Subjects With Refractory Partial Onset Seizures: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Levetiracetam Versus Topiramate as Adjunctive Therapy to Evaluate Efficacy and Safety in Subjects With Refractory Partial Onset Seizures (NCT01229735), a randomized phase 4 study. The primary outcome is Percentage of Subjects Continuing the Allocated Investigational Treatment From the First Study Treatment Intake to Week 52, After the Beginning of Investigational Treatment With Levetiracetam Compared to Topiramate.

2. Clinical Question

The registry describes the purpose as assessing the long-term effect of levetiracetam on retention rate compared with topiramate. Retention is a practical treatment-course outcome: it records whether participants remained on the allocated investigational treatment through the specified follow-up, rather than measuring seizure control alone. The trial also listed outcomes concerning adverse events and seizure frequency, including seizure responders.

The question is comparative, not a test of either medicine against no add-on treatment. Both groups received an investigational drug alongside existing antiepileptic treatment. The registered population was restricted to subjects with refractory partial onset seizures and incomplete control while taking concomitant medication. Findings therefore describe this trial population and its treatment period; the registry record does not establish how the results apply to other populations or treatment settings.

3. Trial Design

This was a randomized, open-label, parallel-group, multicenter Phase IV trial sponsored by UCB Korea Co., Ltd. The registry lists an enrollment of 343 and a completed status. The study began in 2010-11, with primary completion in 2015-05. No masking was used, so participants and study personnel were not blinded to assigned treatment according to the registry classification.

The two groups received levetiracetam or topiramate as adjunctive therapy. The levetiracetam arm used 250 mg and 500 mg tablets, with titration from 1000 mg/day (500 mg bid) to 3000 mg/day (1500 mg bid). The topiramate arm used 25 mg and 100 mg tablets, with titration from 100 mg/day (50 mg bid) to 400 mg/day (200 mg bid). Treatment could continue for up to 52 weeks.

The primary endpoint covered continuation of allocated treatment from first study treatment intake to Week 52. Its analysis population was the Full Analysis Set, defined as members of the Safety Set who returned at least 1 post-baseline seizure diary. The registry lists 176 participants in the levetiracetam primary analysis group and 166 in the topiramate group. These analysis denominators need not equal the overall enrollment: the endpoint is reported for a defined analysis population and the registry record does not provide a complete account of every participant’s movement from enrollment to each analysis set.

Random allocation can support a comparison between groups, while the open-label design means treatment assignment was known. The registry record does not report the allocation ratio, details of the randomization sequence, site count, or the trial’s original sample-size justification. It also does not report a fuller protocol description for titration decisions or treatment discontinuation beyond the arm descriptions and endpoint definition.

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: Participant Flow refers to the Randomized Set which consists of all subjects who were randomized in this study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) consisted of all subjects in the Safety Set who returned at least 1 post-baseline seizure diary.

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 Baseline Characteristics refers to the Safety Set which consists of all subjects who were randomized and received at least 1 dose of trial medication.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Subjects Continuing the Allocated Investigational Treatment From the First Study Treatment Intake to Week 52, After the Beginning of Investigational Treatment With Levetiracetam Compared to Topiramate, measured over From Baseline to Week 52.

The primary endpoint was the percentage of subjects continuing the allocated investigational treatment from the first study treatment intake to Week 52. It is a retention measure: a participant is counted according to whether they continued the assigned treatment over the defined period. The registry reports 59.1% for levetiracetam and 56.6% for topiramate in the Full Analysis Set.

Retention can be useful in a long-term comparison because discontinuation may reflect the combined experience of treatment, including tolerability, seizure control, practical considerations, or other reasons. It is not, by itself, a direct measure of seizure reduction, quality of life, or the reason for stopping. The registry also lists time to discontinuation due to an adverse event as a secondary outcome, which is distinct from the primary continuation percentage: the primary endpoint concerns continuation overall, not only discontinuation attributed to an adverse event.

The reported endpoint is binary at the participant level—continued or did not continue through the stated period—and then expressed as a percentage. That makes the result accessible, but interpretation depends on the event definition, analysis population, handling of incomplete follow-up, and any censoring or missing-data rules. Those detailed rules are not reported in the registry record. The comparison should therefore be read as a contrast between the posted group percentages, alongside the stated analysis, rather than as a complete account of every participant’s treatment history.

7. Results Posted in the Registry

• Topiramate (Full Analysis Set): 56.6% (94/166) versus 59.1% (104/176) on control; risk difference -2.5 percentage points (95% CI -12.9 to 8.0), risk ratio 0.96 (0.80–1.15); unadjusted two-proportion z-test p = 0.645.

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.

Responders Defined as Number of Subjects With at Least 50 % Reduction in the Weekly POS Frequency From Baseline During the Total Treatment Period From Baseline to Week 52

• 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:
  • Topiramate (Full Analysis Set): 64.8% (107/165) versus 69.0% (120/174) on control; risk difference -4.1 percentage points (95% CI -14.1 to 5.9), risk ratio 0.94 (0.81–1.09); unadjusted two-proportion z-test p = 0.421.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Topiramate (Full Analysis Set) and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering adverse events, time to discontinuation due to an adverse event, seizure-frequency change, and a responder definition based on at least 50 % reduction in weekly partial onset seizure frequency. The available secondary information spans treatment tolerability and seizure outcomes, but the record does not provide a complete numerical result for every listed endpoint. Detailed results for time to adverse-event discontinuation and median seizure-frequency reduction are not reported in the registry record.

The posted responder comparison is directionally similar to the primary comparison in that its unadjusted estimate is negative for topiramate relative to levetiracetam, but its confidence interval includes zero. It addresses a different question from retention: a participant can meet a seizure-response threshold without necessarily continuing treatment, and continuation does not itself show seizure response. The secondary result therefore adds context rather than serving as a substitute for the primary endpoint.

Secondary outcomes generally carry less inferential weight than a prespecified primary endpoint, especially when many outcomes are examined. Testing multiple outcomes increases the chance of at least one apparently notable result arising by chance unless the analysis plan accounts for multiplicity. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Any secondary p-values or patterns should therefore be treated cautiously and not as confirmatory evidence on their own.

The adverse-event counts are relevant to the safety profile recorded during the trial, but they do not answer the primary retention question directly. Likewise, a responder outcome focuses on seizure frequency rather than treatment continuation. Considering these measures together can describe different aspects of the trial, while recognizing that incomplete reporting and unreported analysis rules limit the strength of cross-outcome conclusions.

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

• Number of Subjects With at Least One Adverse Event Reported During the Trial Period From Baseline to Week 52
• Time From the First Study Treatment Intake to Drug Discontinuation Due to Adverse Event (AE)
• Median Percent Reduction in the Weekly Partial Onset Seizure (POS) Frequency From Baseline During the Total Treatment Period From Baseline to Week 52
• Responders Defined as Number of Subjects With at Least 50 % Reduction in the Weekly POS Frequency From Baseline During the Total Treatment Period From Baseline to Week 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result is presented in two forms: the registry’s reported logistic regression and an unadjusted recalculation based on the posted group summaries. They answer related comparative questions, but they use different effect scales and should not be conflated. The registry reports an odds ratio of 1.1 with a 95% confidence interval from 0.7 to 1.7 and p = 0.701. The recalculation reports a risk difference for topiramate relative to levetiracetam of -0.025, with a 95% confidence interval from -0.129 to 0.080 and p = 0.645.

What does the risk difference describe?

A risk difference subtracts the event proportion in one group from the event proportion in the comparison group. For this endpoint, the event is continuation of allocated treatment through Week 52. The recalculated estimate is expressed as topiramate relative to levetiracetam, so a negative value corresponds to a lower continuation proportion in the topiramate group in this calculation. This is a simple, unadjusted contrast derived from the posted summaries; it is not an adjusted model estimate.

Its confidence interval describes uncertainty around that estimated difference. Because the interval ranges from -0.129 to 0.080, it includes zero, the value corresponding to no difference on this scale. The interval therefore does not support a precise conclusion about which group has the higher underlying continuation proportion. It also does not demonstrate equivalence, which would require a prespecified equivalence framework and margin; such a margin is not reported in the registry record.

How does an odds ratio differ?

Odds compare the chance of an event with the chance of its absence. An odds ratio compares those odds between groups. It is not the same quantity as a risk difference or a ratio of percentages. The sponsor’s regression result is reported on the odds-ratio scale, whereas the unadjusted recalculation uses a difference in proportions. The registry record does not report the full regression specification, covariates, or all model details, so the adjusted structure of the sponsor’s analysis cannot be reconstructed from the reported summary alone.

The registry’s odds ratio is 1.1, and its 95% confidence interval from 0.7 to 1.7 includes 1, the null value for an odds ratio. Its p-value is 0.701. These features indicate that the reported model did not find a statistically clear departure from its null comparison. The recalculated p-value of 0.645 belongs to the separate unadjusted risk-difference calculation; it is not a substitute for the registry’s model result.

What does a p-value contribute?

A p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. Here, the primary p-values are not small, and both confidence intervals include their respective null values. That pattern is consistent with uncertainty about the direction and magnitude of the between-group difference, not proof of no effect.

Interpretation also depends on design and data handling. Randomization is intended to make treatment groups comparable at baseline, while open-label allocation can influence behavior, reporting, or decisions to discontinue. The registry record does not report details of allocation concealment, missing-data handling, adjustment variables, or the full analysis plan. Those omissions prevent a complete assessment of whether analysis choices could affect the estimates.

The primary endpoint is a participant-level binary outcome summarized as a percentage, and its comparison can be expressed as a difference in proportions or modeled using logistic regression. Different methods can yield different estimates, particularly if the model adjusts for other factors or uses different analysis rules. The registry record provides the sponsor’s reported model estimate and the posted group summaries, but not enough detail to reproduce the model. The unadjusted calculation should therefore be understood as a transparent summary-based comparison, while the registry analysis remains the sponsor’s stated inferential analysis.

For the responder endpoint, the same general distinction applies: the unadjusted risk difference compares the posted responder proportions, whereas a model-based result would depend on its analysis specification. No sponsor-reported analysis is listed for that endpoint. Its recalculated p-value and interval should be treated as exploratory descriptions of the posted summaries, rather than as evidence that the secondary outcome was tested under a fully documented confirmatory plan.

11. Confidence Intervals and Precision

A confidence interval gives a range of estimates compatible with the observed data and the method used to construct the interval. It conveys precision as well as direction: a narrower interval indicates greater precision on that effect scale, while a wider interval leaves more uncertainty about the size and direction of the difference. It does not mean that there is a specified probability that the fixed true effect lies within the particular calculated interval.

For the primary unadjusted risk difference, the estimate is -0.025 and the 95% confidence interval runs from -0.129 to 0.080. The interval includes zero. Thus, the data are compatible with no difference and with differences in either direction on the risk-difference scale. The posted percentages, 59.1% and 56.6%, are point estimates, but they do not capture this uncertainty by themselves.

The sponsor’s logistic regression result has an odds ratio of 1.1, with a 95% confidence interval from 0.7 to 1.7. That interval includes 1, the null value for an odds ratio, and ranges across values on either side of it. This model-based interval should be interpreted on the odds-ratio scale, not as an interval for a percentage-point difference.

The secondary responder recalculation has a risk difference of -0.041, with a 95% confidence interval from -0.141 to 0.059. It too includes zero. These intervals do not establish equivalence, and the registry record does not report a clinically acceptable equivalence margin. They indicate that the estimates are not precise enough to resolve a clear direction of difference from the reported comparisons. The confidence intervals also do not address possible biases arising from missing data, open-label conduct, or unreported analysis choices.

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 effect, not the trial’s original design calculation. For the binary outcomes in this record, the entries refer to participants per arm, not total participants or total events. The assumptions listed for the illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the participants per arm estimated for a planning scenario in which the study would have an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true effect and the assumptions held. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are design calculations, not a measure of what the completed trial achieved.

The rows consider planning for 100%, 75%, or 50% of the observed effect. As the effect used for planning becomes smaller, the required participants per arm increase. This is a general feature of statistical planning: smaller differences are harder to distinguish from sampling variation, so a larger study is typically needed under otherwise comparable assumptions. The primary endpoint illustration uses the observed primary contrast; the secondary responder illustration uses its own observed contrast. The figures are sensitive to those observed estimates and should not be treated as independent evidence about the true effect.

This is not observed power. It is a prospective-style planning illustration calculated from the observed effect and specified assumptions, not a measure of the probability that the trial’s result is correct or of the chance that a future study will reproduce it. The figures should be read as conditional planning scenarios, not as a claim that the original trial was designed around these values.

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 = 0.591; treatment proportion p₁ = 0.566; average p̄ = 0.579.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6983 = 1.3687.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6981 = 0.5875.
4. n = (1.3687 + 0.5875)² / (-0.0246)² = 6,301.0, rounded up to 6,302 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 <- 0.590909090909091                          # control proportion
p1 <- 0.566265060240964                          # 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(1229735)
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 = 6,302 (80% power), 8,435 (90% power)
 75% of observed effect: n per arm = 11,181 (80% power), 14,967 (90% power)
 50% of observed effect: n per arm = 25,104 (80% power), 33,606 (90% power)
power.prop.test: 6301 
Simulated power at n = 6,302 per arm: 0.800 (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 reports the sponsor’s primary analysis as logistic regression, with an odds ratio of 1.1, a 95% confidence interval from 0.7 to 1.7, and p = 0.701. This is the reported model-based result and takes precedence over the unadjusted recalculation when describing the sponsor’s own analysis. Its interval includes the null odds ratio, so the reported analysis does not show a statistically clear difference between groups.

The recalculation uses the posted group summaries to estimate an unadjusted risk difference for topiramate relative to levetiracetam. It gives -0.025, with a 95% confidence interval from -0.129 to 0.080 and p = 0.645. Its direction and broad inferential reading are consistent with the sponsor’s result: neither analysis provides a clear statistical separation between the groups. The estimates are not numerically interchangeable because one is an odds ratio from logistic regression and the other is an unadjusted difference in proportions.

The registry record does not provide the full logistic model specification or enough detail to reproduce the sponsor’s analysis. The recalculation is therefore a check based on the posted summaries, not a replacement for the reported regression. No sponsor-reported statistical analysis is listed for the responder outcome, so its posted unadjusted comparison should not be described as a sponsor model result.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes or comparisons are assessed. Even when each individual test uses a conventional significance threshold, the chance of at least one false-positive finding can increase across a collection of tests. The registry lists multiple secondary outcomes in addition to the primary endpoint. A formal multiplicity strategy—such as an adjustment, testing hierarchy, or designation of selected secondary outcomes as confirmatory—is not reported in the registry record.

This matters most when interpreting secondary findings. A result that appears notable among several tests may be less persuasive if the number of tests and their relationships are not accounted for. The posted responder comparison is an unadjusted recalculation, and no sponsor-reported analysis is listed for it. The registry record does not establish that its secondary outcomes were intended to support confirmatory claims.

Missing-data rules also affect interpretation of a continuation endpoint. The primary analysis population is defined as subjects in the Safety Set who returned at least 1 post-baseline seizure diary. The primary group denominators are 176 for levetiracetam and 166 for topiramate; the responder denominators are 174 and 165. These endpoint-specific analysis populations may differ, but detailed reasons for exclusion or changes in denominators are not reported in the registry record. The handling of participants without a Week 52 assessment, the treatment of incomplete diaries, and any imputation or censoring rules are also not reported in the registry record.

Randomization supports the intended group comparison, but its protection can be weakened if follow-up or outcome availability differs in ways related to treatment or outcome. The posted summaries do not allow those possibilities to be assessed fully. The registry record also does not report the trial’s original statistical analysis plan, interim analyses, or a complete account of prespecified versus exploratory analyses. These gaps do not invalidate the results, but they limit independent evaluation of selection, missingness, and selective reporting.

Because the study was open-label, awareness of treatment assignment could influence participant-reported seizure diaries or decisions to continue treatment. The extent of any such influence cannot be determined from the registry summaries. Interpretation should therefore keep the randomized design in view while also recognizing the possible consequences of unblinded conduct and incomplete reporting.

16. Safety Results

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

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: seizure (3.0%), dizziness (1.1%), duodenal ulcer (0.6%), gastrooesophageal reflux disease (0.6%), pancreatitis acute (0.6%).

The safety information lists serious adverse events affecting 10 of 177 participants in the levetiracetam group and 15 of 166 participants in the topiramate group. Other adverse events are listed for 86 of 177 and 91 of 166 participants, respectively. These are participant counts in the registry’s safety groups; they should not be confused with the primary Full Analysis Set denominators or interpreted as a direct comparison without considering the definitions and follow-up rules.

The most frequent serious-event terms listed include seizure at 3.0%, dizziness at 1.1%, and duodenal ulcer, gastrooesophageal reflux disease, acute pancreatitis, and pneumonia at 0.6% each. The registry record does not provide enough detail in this summary to determine the duration, severity grading, attribution, or overlap of participants across event terms. The death fields are not reported in the registry record.

These figures describe events recorded during the trial; they do not establish that an event was caused by a study drug. Nor do counts alone provide a complete comparative safety analysis. The trial was open-label, and the registry summary does not report adjusted safety comparisons or detailed exposure-adjusted event rates. Safety findings should be read as descriptive information from the posted record, not as individualized guidance.

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

The primary result describes the percentage of participants in each analysis group who continued allocated treatment through Week 52. The posted percentages are 59.1% for levetiracetam and 56.6% for topiramate. The sponsor’s logistic regression and the unadjusted recalculation both have confidence intervals that include their respective null values, and neither provides a statistically clear between-group difference on its reported scale.

That result does not show that the treatments are identical, or that their effects are equivalent. A nonsignificant comparison can reflect a small underlying difference, sampling uncertainty, or limitations in the available data. Equivalence requires a prespecified margin and an analysis designed to assess whether the interval lies within that margin; such a margin is not reported in the registry record.

The primary endpoint is treatment continuation, not seizure reduction. The secondary responder outcome addresses a different aspect of treatment experience, while the adverse-event outcomes describe recorded safety events. These endpoints should not be collapsed into a single measure of benefit or harm. The registry record does not provide complete numerical results for all listed secondary outcomes, and it does not report detailed missing-data rules or the full statistical analysis plan.

The trial’s randomized design supports a comparative interpretation, but its open-label conduct and the incomplete reporting of analysis details qualify that interpretation. The results apply most directly to the enrolled population described in the record: subjects with refractory partial onset seizures not fully controlled with concomitant antiepileptic drugs, treated with the study regimens for up to 52 weeks. The registry record does not establish results for other populations, treatment durations, or clinical decisions.

In practical statistical terms, the observed group percentages are close, while the intervals leave room for differences in either direction. The appropriate conclusion is uncertainty about the comparative retention effect in this trial, rather than a claim that one treatment is superior or that no difference exists. The posted data are descriptive and comparative trial evidence, not medical advice.

18. Why This Trial Matters Statistically

This trial illustrates how the choice of endpoint shapes a comparative question. Treatment retention captures whether participants stayed on their allocated therapy, while seizure response and adverse events describe other dimensions. A retention percentage can be useful for a long treatment period, but it does not identify why participants continued or stopped. Interpretation depends on the endpoint definition and on how incomplete follow-up is handled.

It also demonstrates why effect scale matters. The registry’s logistic regression reports an odds ratio, whereas the summary-based recalculation reports a risk difference. Each conveys a group contrast, but the numerical values have different meanings. Reporting both does not make them interchangeable; rather, it shows why readers should identify the scale, direction, analysis population, and method before interpreting an estimate.

Confidence intervals add essential context to point estimates. The observed retention percentages alone might invite an overly simple reading, but the interval around the unadjusted contrast includes values on both sides of no difference. The same is true of the sponsor’s odds-ratio interval. This uncertainty prevents a confident conclusion about the direction or size of a comparative effect, even though the point estimates are available.

The record also highlights the role of complete reporting. The primary analysis is accompanied by a sponsor-reported model result, but model details, original sample-size assumptions, missing-data rules, and multiplicity procedures are not reported. Secondary outcomes can broaden the clinical picture, yet their interpretation is limited when results or analysis plans are incomplete. Distinguishing what the registry reports from what remains uncertain is central to sound statistical reading.

19. Limitations

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

Several limitations are specific to the information available for this trial. It was open-label, so treatment assignment was known. That could influence participant reporting, study conduct, or decisions to continue or discontinue treatment, although the registry record does not establish whether such effects occurred.

The primary analysis population required membership in the Safety Set and at least 1 post-baseline seizure diary. The record does not describe the disposition of all enrolled participants in enough detail to evaluate how exclusions or incomplete follow-up affected the results. Reasons for discontinuation, the rules for classifying continuation at Week 52, and the handling of missing endpoint data are not reported in the registry record.

The sponsor’s regression result is reported without the full model specification. The registry record does not report the covariates, diagnostics, or other details needed to reproduce that analysis. The unadjusted recalculation is based on posted summaries and cannot address potential imbalances or replace the model-based analysis.

The registry lists several secondary outcomes, but detailed numerical results for time to adverse-event discontinuation and median reduction in seizure frequency are not reported in the registry record. A multiplicity strategy and the full statistical analysis plan are also not reported. The original sample-size justification and interim-analysis information are not reported in the registry record; the planning illustrations should not be mistaken for the trial’s design assumptions.

Finally, the results are tied to the registered population, add-on regimens, and treatment period. The record does not establish how well they generalize beyond subjects with refractory partial onset seizures receiving concomitant antiepileptic drugs. The study’s multicenter status is recorded, but the site count is not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Levetiracetam Versus Topiramate as Adjunctive Therapy to Evaluate Efficacy and Safety in Subjects With Refractory Partial Onset Seizures — NCT01229735.
• Registry record last updated 2017-08-15; status last verified 2017-07.
• Results first posted 2016-02-12.
• 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

This completed randomized, open-label, parallel-group Phase IV trial compared levetiracetam with topiramate as adjunctive therapy for refractory partial onset seizures. Enrollment was 343, and treatment could continue for up to 52 weeks. The primary endpoint was the percentage continuing allocated treatment through Week 52.

The registry reports continuation of 59.1% among 176 participants in the levetiracetam Full Analysis Set and 56.6% among 166 participants in the topiramate Full Analysis Set. The sponsor’s logistic regression reported an odds ratio of 1.1, with a 95% confidence interval from 0.7 to 1.7 and p = 0.701. The unadjusted recalculation likewise had a confidence interval including no difference.

The record also lists seizure-response and safety outcomes, but not all secondary results or analysis details are available. Missing-data procedures, multiplicity handling, and the original sample-size justification are not reported in the registry record. The posted comparisons therefore indicate uncertainty about the relative continuation effect, rather than establishing superiority or equivalence.