Long-Term Study of Gabapentin Enacarbil (GEn, XP13512) vs. Placebo in Patients With Restless Legs Syndrome.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Long-Term Study of Gabapentin Enacarbil (GEn, XP13512) vs. Placebo in Patients With Restless Legs Syndrome. (NCT00311363), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Experienced a Relapse During the Double-Blind Treatment Period.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, double-blind, parallel-group study sponsored by XenoPort, Inc. Its official title describes a long-term comparison of XP13512 with placebo intended to assess maintenance of efficacy and safety in patients with restless legs syndrome. The brief study summary identifies once-daily GEn as the treatment of interest. The primary endpoint concerns relapse over the double-blind treatment period, from randomization at Week 24 through the end of treatment, with the specified timeframe recorded as Days 169 to 252 (Weeks 24 to 36).

The registry record reports 327 participants enrolled, a study start of 2006-04, primary completion in 2007-11, and completed status. For the primary endpoint, the DB ITT population comprised participants randomized into the study, exposed to at least part of a dose of double-blind study drug, and assessed at least once after randomization for both IRLS total score and investigator-rated CGI-C. The posted primary endpoint groups were DB placebo, with 97 participants, and DB GEn 1200 mg, with 96 participants. These group counts are the endpoint denominators, not the overall enrollment count.

The registry lists GEn (XP13512) and placebo interventions, and its arm descriptions identify GEn 1200 mg and placebo. The safety results additionally distinguish a single-blind GEn group from the double-blind GEn and placebo groups. The record does not describe the full sequence of treatment periods, the allocation ratio, the randomization procedure, or masking procedures beyond identifying the study as randomized and double-blind. Its detailed protocol, the original sample-size justification, and further operational design specifications are not reported in the registry record. The design label and the arm descriptions establish the broad comparison, but they do not answer every question about how participants moved through the study or how treatment allocation was implemented.

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: There were 27 participants who completed the Single-blind Treatment Period who either elected not to enroll into the Double-blind Treatment Period or were considered non-responders and were not randomized.

24-Week Single-Blind Treatment Period

Reasons for not completing this period:

12-Week Double-Blind Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Double-blind Intent-to-Treat (DB ITT) Population: all participants who were randomized into the study, received at least one dose (or any portion of dose) of DB study drug, and for whom at least one post-Randomization visit (Week 24) IRLS Scale total score and investigator-rated CGI-C was available. One participant did not satisfy this description.

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: Single-blind (SB) Safety Population: subjects who received at least 1 dose of SB study drug 1 subject withdrew from the SB period prior to receiving drug due to protocol non-compliance, and thus was excluded from the SB-Safety Population

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Experienced a Relapse During the Double-Blind Treatment Period, measured over DB Treatment Period; Days 169 to 252 (Weeks 24 to 36).

The primary endpoint is the percentage of participants who experienced a relapse during the double-blind treatment period, recorded for Days 169 to 252 (Weeks 24 to 36). A relapse was defined as worsening of RLS symptoms or withdrawal due to lack of efficacy. Worsening was not based on a single symptom judgment: it required an increase in total IRLS score of at least 6 or more points relative to the randomization score, an IRLS score of at least 15, and an investigator-rated CGI-C assessment of “much worse” or “very much worse.” These criteria make the endpoint a composite event definition combining a symptom scale, a score threshold, and a clinician assessment. Withdrawal because of lack of efficacy also counted as relapse.

For a maintenance-of-efficacy question, a relapse endpoint focuses on whether participants met a predefined threshold for worsening during continued treatment, rather than only on a mean score at one assessment. The percentage expresses how common the defined event was in each group during the specified period. The endpoint is binary at the participant level: a participant either met the relapse definition or did not. Its interpretation depends on the record’s event criteria and the population assessed; it is not a direct measure of every dimension of RLS symptoms or of treatment experience. The registry record specifies the DB ITT population and its assessment requirements, but the primary endpoint’s missing-data handling and any additional rules for classifying incomplete follow-up are not reported in the registry record.

7. Results Posted in the Registry

• DB GEn 1200 mg: 9.4% (9/96) versus 22.7% (22/97) on control; risk difference -13.3 percentage points (95% CI -23.5 to -3.1), risk ratio 0.41 (0.20–0.85); unadjusted two-proportion z-test p = 0.012.

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.

Percentage of Participants Who Responded to Treatment Based on Scores on the Investigator-Rated Clinical Global Impression of Change (CGI-C) Scale as a Dichotomous Variable at Week 36 (DB Treatment Phase) Using LOCF

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • DB GEn 1200 mg: 75.0% (72/96) versus 67.0% (65/97) on control; risk difference 8.0 percentage points (95% CI -4.8 to 20.7), risk ratio 1.12 (0.93–1.34); unadjusted two-proportion z-test p = 0.221.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DB GEn 1200 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Responded to Treatment Based on Scores on the Participant-Rated CGI-I at Week 36 (DB Treatment Phase) Using LOCF

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • DB GEn 1200 mg: 87.5% (84/96) versus 79.4% (77/97) on control; risk difference 8.1 percentage points (95% CI -2.3 to 18.5), risk ratio 1.10 (0.97–1.25); unadjusted two-proportion z-test p = 0.129.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DB GEn 1200 mg and the control. The interval gives the range of effects that remain compatible with the data.

The selected secondary findings are directionally consistent with higher response percentages in the GEn group than in the placebo group for both investigator-rated CGI-C response and participant-rated CGI-I response. Their risk-difference confidence intervals include zero, and the posted unadjusted p-values are 0.221 and 0.129. This means the estimates remain compatible with no group difference under the displayed interval approach, even though their point estimates favor GEn. They measure response classifications rather than the primary endpoint’s defined relapse event, so they add related but not identical information.

The primary result concerns a relapse definition that combines a threshold change in IRLS score, an absolute IRLS threshold, and a CGI-C judgment, while also counting withdrawal due to lack of efficacy. The secondary response outcomes instead classify whether participants met specified investigator- or participant-rated response criteria at Week 36 or the end of double-blind treatment, using LOCF. These different outcome definitions and approaches can yield distinct estimates without being contradictory. The record also lists other secondary outcomes, including time to relapse and changes in symptom or sleep-related measures, but their numerical results are not reported in the registry record.

Secondary results carry less weight as confirmatory evidence when many outcomes are examined and no multiplicity strategy is reported. The registry lists 33 outcome measures and 32 secondary outcomes posted, while the multiplicity procedure is not reported in the registry record. Without a reported hierarchy or adjustment, unadjusted secondary p-values do not account for the broader set of comparisons. They are useful as supporting context and for describing patterns, but they should not be treated as independent confirmation of the primary finding. The broader pattern is therefore one of secondary point estimates favoring GEn on the two response measures, with intervals that remain uncertain about whether the underlying response difference is nonzero.

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

• Time From Randomization to Relapse in RLS Symptoms During the Double-Blind Treatment Period
• Time From Randomization to Relapse in RLS Symptoms During the Double-Blind Treatment Period (Excluding First Two Weeks of DB Phase)
• Mean Change From Randomization to Week 36 (or End of Treatment) in the IRLS Rating Scale (IRLS) Total Score Using Last Observation Carried Forward (LOCF)
• Percentage of Participants Who Responded to Treatment Based on Scores on the Investigator-Rated Clinical Global Impression of Change (CGI-C) Scale as a Dichotomous Variable at Week 36 (DB Treatment Phase) Using LOCF
• Number of Participants in Each Category of the Investigator-Rated CGI-C at Week 36 (DB Treatment Phase) Using LOCF
• Number of Participants in Each Category of the Participant-Rated CGI-I Scale at Week 36 (DB Treatment Phase) Using LOCF
• Percentage of Participants Who Responded to Treatment Based on Scores on the Participant-Rated CGI-I at Week 36 (DB Treatment Phase) Using LOCF
• Mean Change From Randomization to Week 36 (DB Treatment Phase) in the Mean Daytime Somnolence Domain Score of the Medical Outcomes Study (MOS) Sleep Scale Using LOCF

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary percentage: each participant in the endpoint population is classified according to whether a relapse occurred during the specified double-blind period. The group percentages describe the observed frequency of that classification. A risk difference compares those frequencies by subtracting the placebo risk from the GEn risk; negative values in this comparison indicate a lower observed event frequency in the GEn group. The posted unadjusted re-calculation is -0.133. This is an absolute-scale comparison, unlike a relative measure such as a risk ratio or an odds ratio.

The sponsor reported an odds ratio from logistic regression. Logistic regression is a general method for modeling the odds of a binary outcome. An odds ratio compares the outcome odds between groups; a value below one in the reported GEn-versus-placebo comparison indicates lower odds in the GEn group. Odds are not the same quantity as probabilities or risks, so an odds ratio should not be read as a percentage-point difference. The reported odds ratio is 0.353, with a 95% confidence interval from 0.2 to 0.8. The re-calculated odds ratio is 0.353, with a confidence interval from 0.153 to 0.813. The sponsor’s result is the reported model-based analysis; the re-calculation is unadjusted and uses the posted counts.

What a confidence interval conveys

In general, a confidence interval describes the uncertainty around an estimated effect under the assumptions of the statistical procedure. It gives a range of effect values compatible with the data and method, rather than identifying a single exact underlying effect. For the primary risk difference, the posted interval runs from -0.235 to -0.031. Because this range remains on the negative side of zero, it is consistent with a lower observed relapse risk for GEn on the risk-difference scale. The interval’s breadth also matters: estimates within the range imply different magnitudes, so the point estimate alone does not capture the uncertainty.

A p-value summarizes how unusual results at least as incompatible with a specified null hypothesis would be under that hypothesis and the analysis assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The posted unadjusted p-value for the risk-difference re-calculation is 0.012. The sponsor’s logistic-regression analysis reports p = 0.016. These values arise from different analysis approaches and should be read with their corresponding effect estimates and intervals, rather than treated as interchangeable measures of effect.

Why analysis scale and model matter

The risk difference presents an absolute contrast in event frequency. The odds ratio presents a relative contrast in odds. Different scales answer related but not identical questions, and their values cannot be compared numerically as though they were the same measure. Logistic regression can model a binary endpoint and can incorporate covariates when specified, but the registry record does not report the covariates or other model details. It identifies regression, logistic, and reports an odds ratio. The re-calculation is explicitly unadjusted; it uses the posted group summaries rather than a participant-level fitted model.

When count outcomes show greater variability than a simple model assumes, over-dispersion can make standard errors too small and intervals too narrow if it is ignored. That is a general statistical concern, not a feature established for this binary endpoint. The registry record does not report an over-dispersion assessment, and the primary endpoint is analyzed as a binary participant-level event. No claim about over-dispersion or a correction for it can be made from the reported information.

Population and endpoint definition

The DB ITT population is defined in the registry as randomized participants who received at least part of a dose of double-blind study drug and had at least one post-randomization IRLS score and investigator-rated CGI-C assessment. This definition is narrower than simply all enrolled participants. The endpoint’s relapse rule combines symptom worsening and withdrawal due to lack of efficacy. The symptom-worsening rule requires all of its stated score and CGI-C conditions. Such a composite definition can capture more than one way of meeting the outcome, but its meaning is tied to the listed criteria and assessment period.

The registry names LOCF for several secondary outcomes. LOCF means last observation carried forward: in general, an earlier recorded value is used as the outcome at a later target time when a later measurement is unavailable, according to the analysis rule. Its use can affect estimates when measurements are missing, and it relies on assumptions about how the unobserved later value relates to the last observed value. The record identifies LOCF for listed secondary analyses, but the primary endpoint’s missing-data method and detailed implementation of secondary LOCF are not reported in the registry record. It is therefore not appropriate to assume the primary endpoint used the same method.

The registry lists 33 outcome measures and 32 secondary outcomes posted. Considering multiple outcomes raises the possibility that some apparent differences arise by chance when many hypotheses are examined. Statistical adjustment or a prespecified hierarchy can address aspects of this issue, but neither a multiplicity strategy nor its details are reported in the registry record. This limits how strongly individual secondary p-values should be interpreted. The primary and secondary findings also differ in what they measure: the primary endpoint is a defined relapse event, while selected secondary endpoints are response classifications based on investigator or participant ratings.

Finally, a planning calculation based on an observed effect is not a retrospective measure of the probability that the completed study detected a true effect. It asks how many participants a hypothetical study would require under stated assumptions to target a selected effect and power. The posted planning illustration uses a two-sided significance level of 0.05, equal allocation, and a normal approximation. The trial’s original sample-size assumptions are not reported in the registry record, so the illustration should not be mistaken for the design rationale or conduct of this study.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.133, with a 95% confidence interval from -0.235 to -0.031. The interval lies below zero, supporting the direction of the observed comparison: fewer recorded relapses in the GEn group than the placebo group. It also spans a range of possible absolute differences, so the data do not pinpoint one exact magnitude. The estimate should be read alongside the endpoint definition, group sizes, and analysis population, rather than as a stand-alone measure.

For the odds-ratio scale, the sponsor reports 0.353, with a 95% confidence interval from 0.2 to 0.8. The unadjusted re-calculation is 0.353, with an interval from 0.153 to 0.813. These estimates are close in direction and central value, while the sponsor’s interval is reported at a coarser precision. The odds-ratio interval also lies below one, consistent with lower observed relapse odds for GEn in the reported comparison. The risk-difference and odds-ratio intervals describe uncertainty on different scales and should not be compared by their numerical widths.

Confidence intervals are not guarantees that the true effect lies in the displayed range. In general, they express the uncertainty produced by a particular method and its assumptions. The registry record does not provide enough detail to assess every modeling choice, missing-data assumption, or sensitivity analysis. The primary endpoint denominators are 97 for placebo and 96 for GEn 1200 mg; the overall enrollment is 327. The registry record does not explain fully why the endpoint population differs from total enrollment, so the interval’s precision should be understood in the context of the analyzed population rather than the enrollment total alone.

The selected secondary response estimates have intervals that include no difference: -0.048 to 0.207 for the investigator-rated CGI-C response risk difference, and -0.023 to 0.185 for the participant-rated CGI-I response risk difference. Those intervals allow both little or no difference and differences favoring either group. They are less precise about the direction than an interval that stays entirely on one side of zero. Since multiple secondary outcomes are listed and multiplicity handling is not reported in the registry record, these intervals and their associated unadjusted tests are best treated as exploratory context rather than independent confirmation of the primary endpoint.

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 posted planning estimates are participants per arm for this binary outcome. They are not total-event counts. The accompanying curve represents the same planning exercise across the stated effect assumptions. The estimates assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each scenario, the target effect is the stated fraction of the observed effect. These assumptions describe the planning illustration; the trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning method estimates would be needed for an 80% chance of detecting the specified effect, if that effect and the assumptions used for the calculation were correct. The 90% power column gives the corresponding per-arm estimate for a 90% chance. Power is a property of a planned design under assumptions; it is not a measure of how likely the observed result is to be true. The displayed figures are planning illustrations based on the observed effect, not observed power for the completed trial.

The rows planning for 100% of the observed effect use the full estimated effect as the target. The rows planning for 75% and 50% of the observed effect consider smaller target effects. Smaller effects are harder to distinguish from random variation, so detecting them generally requires more participants. Accordingly, the planning estimates increase as the target effect is reduced. The estimates are hypothetical design quantities and do not establish what enrollment would have been appropriate for a future study, especially if the true effect or assumptions differ from those used in the illustration.

The primary endpoint groups included 97 placebo participants and 96 GEn participants. Those realized endpoint group sizes should not be read as a direct validation or failure of the planning illustration: the illustration uses the observed effect to explore hypothetical sample sizes, while the record does not report the original calculation or its assumptions. The planning figures also should not be confused with the sponsor’s logistic-regression analysis or the unadjusted effect re-calculation. Each answers a different statistical question.

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 = 0.227; treatment proportion p₁ = 0.094; average p̄ = 0.160.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5188 = 1.0169.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5102 = 0.4294.
4. n = (1.0169 + 0.4294)² / (-0.1331)² = 118.2, rounded up to 119 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 <- 0.22680412371134                          # control proportion
p1 <- 0.09375                          # 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(311363)
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 = 119 (80% power), 158 (90% power)
 75% of observed effect: n per arm = 229 (80% power), 306 (90% power)
 50% of observed effect: n per arm = 553 (80% power), 740 (90% power)
power.prop.test: 118.2 
Simulated power at n = 119 per arm: 0.815 (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 reported primary analysis used logistic regression and reported an odds ratio of 0.353, with a 95% confidence interval from 0.2 to 0.8 and p = 0.016. The unadjusted re-calculation from the posted group counts gives an odds ratio of 0.353, with an interval from 0.153 to 0.813. These estimates have a similar central value and the same direction, with the reported comparison indicating lower odds of relapse for GEn than placebo.

The re-calculation also presents the comparison as a risk difference: -0.133, with a 95% confidence interval from -0.235 to -0.031 and an unadjusted p-value of 0.012. That measure is an absolute contrast in event frequency, whereas the sponsor’s odds ratio is a relative contrast in odds. The sponsor’s p-value and the re-calculated p-value need not match because the analyses use different statistical approaches and effect scales. The sponsor’s analysis is the trial’s reported analysis; the re-calculation is a simple unadjusted analysis based on the posted summaries. The registry record does not detail the logistic-regression model beyond naming the method and effect measure, so the role of any covariate adjustment is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 33 outcome measures, including 32 secondary outcomes posted. The primary outcome is the percentage of participants with a relapse during the double-blind treatment period. A substantial range of secondary outcome types is also identified, including time to relapse, symptom-score change, investigator- and participant-rated response or category outcomes, and a daytime somnolence domain score. The registry record does not report whether the study used a prespecified testing hierarchy, a family-wise error procedure, false-discovery control, or another approach to multiplicity. Without that information, individual secondary p-values should be interpreted cautiously; unadjusted findings do not account for the number of outcomes considered.

The primary endpoint population is specifically defined as randomized participants who received at least part of a double-blind dose and had at least one post-randomization Week 24 IRLS total score and investigator-rated CGI-C assessment. The primary group denominators are 97 for placebo and 96 for GEn 1200 mg. This analysis population definition should not be casually equated with all 327 enrolled participants. The registry record does not report a full accounting of exclusions, missing assessments, withdrawals, or the reasons that enrollment and endpoint denominators differ.

Some secondary outcome descriptions explicitly specify LOCF. In general, last observation carried forward uses a participant’s last available value in place of a missing value at a later target assessment, according to the analysis rule. The record does not provide enough detail to assess its implementation, the amount or pattern of missing data, or whether alternative missing-data analyses were conducted. The primary endpoint description does not identify a missing-data method, so it is not reported in the registry record whether the primary analysis used LOCF or another approach. Additional sensitivity analyses, protocol-deviation rules, and handling of intercurrent events are also not reported in the registry record.

The absence of these details does not itself show that the analysis was invalid. It means that the registry-level information cannot establish how multiplicity and missingness were addressed beyond the population and outcome descriptions that are recorded. Those uncertainties are especially relevant when interpreting secondary results and when considering how far the primary estimate can be generalized beyond participants with the required assessments.

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: convulsion (1.0%), anaphylactic reaction (1.0%), diverticulitis (1.0%), angina pectoris (0.3%), chest pain (0.3%).

The safety results distinguish a single-blind GEn group from the double-blind placebo and GEn groups. Serious adverse events were recorded for 3 of 326 participants at risk in the single-blind GEn group, 2 of 98 at risk in the double-blind placebo group, and 1 of 96 at risk in the double-blind GEn group. Other adverse events were recorded for 179 of 326, 15 of 98, and 13 of 96 participants at risk, respectively. These are counts within the registry’s stated groups; they are not the primary efficacy outcome.

The top serious-event terms listed in the record include Convulsion, Anaphylactic Reaction, and Diverticulitis, each reported as 1.0%, along with Angina Pectoris, Chest Pain, and Injury Asphyxiation, each reported as 0.3%. The record does not associate these listed terms with a particular treatment group in the posted summary, so they should not be assigned to one. Death counts are not reported in the registry record.

The single-blind and double-blind groups differ in size and treatment period, so the counts should not be compared as if they came from identical exposure conditions. The registry information does not provide event timing, duration of exposure, severity breakdowns beyond the serious-event designation, or a detailed account of whether events were considered related to study drug. These figures describe the recorded adverse-event counts and do not, by themselves, establish a causal treatment relationship or provide a complete safety profile.

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

The primary data show that the recorded relapse percentage during the double-blind treatment period was lower in the GEn 1200 mg group than in the placebo group: 9.4% versus 22.7%. The unadjusted risk-difference estimate is -0.133, and its 95% confidence interval, -0.235 to -0.031, remains below zero. The sponsor’s logistic-regression result also points toward lower relapse odds in the GEn group, with an odds ratio of 0.353 and a 95% confidence interval from 0.2 to 0.8. These are statistical descriptions of the posted results, not a recommendation about treatment.

The endpoint reflects a specific operational definition of relapse and a defined double-blind period. It does not summarize every aspect of RLS symptoms, participant experience, long-term functioning, or outcomes outside the recorded measures. The primary endpoint population also required at least one post-randomization IRLS assessment and investigator CGI-C assessment, so the reported percentages describe that defined analysis population. The registry record does not fully account for all enrolled participants in relation to those endpoint denominators.

The estimates have uncertainty. The confidence interval for the risk difference indicates a range of plausible values under the analysis method, rather than a single exact effect. The secondary response estimates are less conclusive: their intervals include no difference, and the registry record does not report multiplicity handling. They should be understood as additional, distinct outcome measurements rather than as definitive validation of a broad effect across the range of outcomes.

The results do not establish why participants did or did not relapse, how the primary estimate would change under other missing-data assumptions, or whether results extend to people or treatment periods not represented by the endpoint population and timeframe. The record does not report the original sample-size rationale, detailed model specifications, or sensitivity analyses. Those omissions limit the questions that can be answered from the registry record. A statistical difference on a defined endpoint is not, on its own, a complete account of clinical importance, safety, durability beyond the recorded period, or individual outcomes.

18. Why This Trial Matters Statistically

This trial illustrates the distinction between an outcome’s operational definition and the broader clinical concept it is intended to represent. Relapse was not a general impression alone: it combined specified IRLS score criteria with an investigator CGI-C judgment, and the definition also counted withdrawal because of lack of efficacy. That combination matters because the estimated group difference applies to participants meeting the registry’s particular event rule during the double-blind period.

It also demonstrates why effect scale matters. A risk difference describes an absolute contrast in event percentages, while an odds ratio describes a relative contrast in odds. The sponsor’s logistic-regression result and the unadjusted risk-difference re-calculation have different scales and methods, yet they point in the same direction. Reading both helps distinguish the reported model-based result from a simple comparison of observed group summaries, without treating their numerical values as interchangeable.

The confidence interval is central to the interpretation. The primary risk-difference interval remains below zero, while the selected secondary response intervals include zero. This contrast shows why the point estimate alone is insufficient and why uncertainty should be considered separately for each endpoint. The multiple listed outcomes also make multiplicity relevant; because the registry record does not report a correction or testing hierarchy, secondary findings warrant more cautious interpretation than a prespecified primary comparison.

Finally, the study record separates overall enrollment from the population available for the primary endpoint, and it names LOCF for some secondary outcomes without reporting a primary missing-data method. These details underscore that analysis populations and missing-data handling are part of the meaning of a result, not merely technical footnotes. The trial is therefore useful statistically as an example of interpreting a binary primary outcome, comparing absolute and relative effect measures, and keeping secondary analyses and planning illustrations in their proper context.

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.

The registry record does not report the original sample-size justification or the assumptions used when the trial was designed. The posted planning illustration is based on the observed effect and cannot fill that gap. Detailed randomization procedures, allocation ratio, model covariates, and additional logistic-regression specifications are also not reported in the registry record.

The primary analysis population required post-randomization IRLS and CGI-C assessments, and its group sizes were 97 and 96, compared with 327 participants enrolled overall. The record does not give a full participant flow or explain the difference, so the extent and reasons for exclusions or missing endpoint data cannot be determined from the registry information. The primary missing-data method and sensitivity analyses are not reported in the registry record. LOCF is named for some secondary outcomes, but the details of its application and the amount or pattern of missing data are not given.

Multiplicity handling is not reported despite the listing of numerous outcomes. This limits the strength of confirmatory claims based on secondary results. The numerical results for most of the listed secondary outcomes are not reported in the registry record, so a complete assessment of consistency across all measures is not possible from the available information. The trial’s detailed protocol, adherence information, reasons for treatment discontinuation beyond the relapse definition, and protocol-deviation handling are also not reported in the registry record.

The safety summary separates single-blind GEn from the double-blind groups, and the populations and group sizes differ. It provides counts, but the registry summary does not provide the timing or duration of each event, a complete treatment-relatedness assessment, or death counts. The listed serious-event terms are not linked to treatment groups in the posted summary. Consequently, the safety information supports description of the recorded counts, but not a comprehensive comparison of safety profiles.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Long-Term Study of Gabapentin Enacarbil (GEn, XP13512) vs. Placebo in Patients With Restless Legs Syndrome. — NCT00311363.
• Registry record last updated 2013-07-22; status last verified 2011-05.
• Results first posted 2011-05-25.
• 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

NCT00311363 is a completed phase 3 randomized, double-blind, parallel-group study of GEn (XP13512) versus placebo in participants with restless legs syndrome. The registry record reports 327 participants enrolled. The primary outcome was relapse during the double-blind treatment period, defined using IRLS and investigator-rated CGI-C criteria and including withdrawal due to lack of efficacy.

Relapse was recorded for 22.7% of the DB placebo group and 9.4% of the DB GEn 1200 mg group. The posted unadjusted risk difference is -0.133, with a 95% confidence interval from -0.235 to -0.031. The sponsor’s logistic-regression analysis reports an odds ratio of 0.353, with a 95% confidence interval from 0.2 to 0.8 and p = 0.016. Selected secondary response estimates are directionally higher for GEn, but their confidence intervals include no difference. Multiplicity handling, primary missing-data procedures, and the original sample-size rationale are not reported in the registry record.