Long Term Study Of Pregabalin In Idiopathic Restless Legs Syndrome Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Long Term Study Of Pregabalin In Idiopathic Restless Legs Syndrome Patients (NCT00806026), a randomized phase 3 study. The primary outcome is Restless Legs Syndrome (RLS) Symptom Severity.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, double-blind, parallel-group study with an enrollment of 731. The registry title describes a 12-month study of pregabalin in people with restless legs syndrome, and its brief summary states that the aim was to investigate efficacy and tolerability for up to 12 months. The condition is identified as idiopathic restless legs syndrome. The registry record lists the study as completed, with a start of 2008-12 and primary completion in 2011-05.

The named treatment groups include pregabalin 300 mg, pramipexole 0.25 mg, pramipexole 0.5 mg and placebo. The arm descriptions also include placebo-to-treatment groups for pregabalin and both pramipexole doses. Descriptions of what happened within those sequences are not reported in the registry record, so the arm names alone do not establish further details of treatment timing or transition procedures.

The posted primary outcome is a baseline mean score, while the selected secondary measures include baseline sleep measures and outcomes at Week 12. Thus, the registry’s broad 12-month study purpose and the time points represented in the posted results are not the same thing. The primary results presented are baseline summaries, not an estimate of a treatment-related change over the study period. The number of participants analyzed also differs among the reported outcome groups. Details of the original allocation ratio, concealment procedures, dose adjustments, follow-up schedule, and the full statistical analysis plan are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population included all randomized participants who took at least 1 dose of study medication and had at least one post-randomization efficacy assessment on any efficacy scale. Here, the 'N' (number of participants analyzed) is signifying those participants who were evaluable for this measure for each group respectively.

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.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Restless Legs Syndrome (RLS) Symptom Severity, measured over Baseline.

The primary measure is the International Restless Legs Syndrome Study Group Rating Scale, or IRLS. It is a clinician-administered instrument intended to assess the severity of restless legs syndrome symptoms and their impact on daily living. The registry describes 10 items scored from 0 to 4, with a global score ranging from 0 to 40. Lower values indicate lower symptom severity and impact, and better quality of life according to the registry description.

The scale also has a symptom-severity subscale based on 6 items, ranging from 0-24, and an impact-on-daily-living subscale based on 3 items, ranging from 0-12. Lower values indicate less severity or impact on the corresponding subscale. The registry notes that item 3 is unrelated to the other items. The global score uses all 10 items.

This instrument is used because it provides a structured clinical measure of RLS symptoms and their effects, rather than relying only on a single symptom question. However, the primary outcome reported for this trial is the mean score at baseline. That is useful for describing the groups at the recorded starting assessment, but it is not a measure of improvement or deterioration during treatment. The registry record does not report a primary-outcome treatment comparison at a later time point in the primary results.

7. Results Posted in the Registry

• Pregabalin 300 mg: mean 22.30 versus 22.40 on control; difference -0.10 (95% CI -1.29 to 1.09), standardized effect d = -0.02; z-test p = 0.869.
• Pramipexole 0.25 mg: mean 22.40 versus 22.40 on control; difference 0.00 (95% CI -1.16 to 1.16), standardized effect d = 0.00; z-test p = 1.000.
• Pramipexole 0.5 mg: mean 22.10 versus 22.40 on control; difference -0.30 (95% CI -1.43 to 0.83), standardized effect d = -0.06; z-test p = 0.603.

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.

Subjective Sleep Questionnaire (SSQ): Subjective Waking After Sleep Onset (WASO)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Pregabalin 300 mg: mean 90.60 versus 79.50 on control; difference 11.10 (95% CI -4.63 to 26.83), standardized effect d = 0.15; z-test p = 0.167.
  • Pramipexole 0.25 mg: mean 100.20 versus 79.50 on control; difference 20.70 (95% CI 3.54 to 37.86), standardized effect d = 0.26; z-test p = 0.018.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pregabalin 300 mg 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 mean is statistically higher for Pramipexole 0.25 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in SSQ: Subjective WASO at Week 12

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Pregabalin 300 mg: mean -49.86 versus -32.61 on control; difference -17.25 (95% CI -25.79 to -8.71), standardized effect d = -0.44; z-test p = <0.001.
  • Pramipexole 0.25 mg: mean -33.69 versus -32.61 on control; difference -1.08 (95% CI -9.74 to 7.58), standardized effect d = -0.03; z-test p = 0.807.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Pregabalin 300 mg 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 Pramipexole 0.25 mg and the control. The interval gives the range of effects that remain compatible with the data.

Subjective Sleep Questionnaire (SSQ): Latency Subscale Score at Week 12

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Pregabalin 300 mg: mean 41.60 versus 47.70 on control; difference -6.10 (95% CI -14.82 to 2.62), standardized effect d = -0.15; z-test p = 0.170.
  • Pramipexole 0.25 mg: mean 43.10 versus 47.70 on control; difference -4.60 (95% CI -13.41 to 4.21), standardized effect d = -0.11; z-test p = 0.306.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pregabalin 300 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pramipexole 0.25 mg and the control. The interval gives the range of effects that remain compatible with the data.

The selected secondary measures address related but distinct aspects of sleep: waking after sleep onset, the time to fall asleep, hours of sleep, awakenings, sleep quality and next-day impact. The registry lists 18 posted secondary outcomes, while the broader record lists 22 outcome measures. These measures extend beyond the clinician-rated primary scale, but they do not all capture the same construct or use the same timeframe. Baseline sleep summaries describe starting levels; Week 12 and change-from-baseline outcomes describe later measurements or changes.

Across the selected results, the pattern is not uniform across outcomes or treatment comparisons. Some estimates favor a lower value relative to placebo, some are close to zero, and their intervals differ in whether they include zero. For the Week 12 change in subjective waking after sleep onset, the posted model-based result for pregabalin is more clearly separated from zero than the result for pramipexole 0.25 mg. That isolated contrast should be interpreted as one secondary finding within a wider set of measurements, rather than as confirmation of the primary result.

The relation to the primary outcome is limited by the fact that the primary result is a baseline IRLS score, not a later treatment contrast. A sleep measure can offer complementary information about participants’ experience, but it does not substitute for a treatment effect on the primary endpoint. Nor does a favorable estimate on one sleep outcome establish a consistent pattern across the other measures.

Unadjusted secondary results carry less weight because many outcomes, time points and comparisons create multiple opportunities for a nominally notable finding. The registry record does not report a multiplicity adjustment or a hierarchy that would identify which secondary tests were confirmatory. The observed pattern is therefore best treated as descriptive and hypothesis-generating unless supported by a prespecified analysis plan that is not reported in the registry record. The complete secondary outcome set, rather than one selected comparison, is relevant to judging consistency.

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

• Subjective Sleep Questionnaire (SSQ): Subjective Waking After Sleep Onset (WASO)
• Change From Baseline in SSQ: Subjective WASO at Week 12
• Subjective Sleep Questionnaire (SSQ): Latency Subscale Score at Week 12
• Subjective Sleep Questionnaire (SSQ): Hours of Sleep Subscale Score at Week 12
• Subjective Sleep Questionnaire (SSQ): Number of Awakenings Subscale Score at Week 12
• Subjective Sleep Questionnaire (SSQ): Quality of Sleep Subscale Score at Week 12
• RLS-Next Day Impact (RLS-NDI)
• Change From Baseline in RLS-NDI at Week 12

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference represent?

A mean is the arithmetic average of a continuous measure across the participants included in a group’s analysis. In the primary outcome, the measure is the IRLS score; in the selected sleep outcomes, the units include minutes or scale scores. A mean difference compares the average in one group with the average in the placebo group. The sign depends on the subtraction order used in the reported comparison. The registry’s listed primary comparisons are expressed as the treatment-group mean relative to placebo. A negative difference therefore indicates a lower posted mean in that treatment group, not necessarily a favorable treatment effect. The meaning depends on the outcome and, critically, its timeframe.

For the baseline primary endpoint, the differences describe how the groups’ starting means compare. They do not estimate change after treatment. For an outcome defined as change from baseline, the comparison instead concerns group differences in the recorded change. These are distinct estimands: one is a comparison of baseline levels, and the other is a comparison of change over the stated measurement interval.

What does the standard deviation describe?

The standard deviation describes how dispersed participant scores are around a group mean. A larger standard deviation means more variability among the observed values; it is not the uncertainty of the mean itself. The primary outcome reports means and standard deviations. Some secondary outcomes instead report least-squares means and standard errors. A standard error describes the estimated precision of a mean or model-based estimate, rather than the spread of individual participant values. These two dispersion measures should not be read as interchangeable.

How should confidence intervals and p-values be read?

A confidence interval gives a range of values compatible with the estimate under the statistical model and its assumptions. For a mean difference, an interval that includes zero indicates that no difference is among the values compatible with the interval at the stated confidence level. An interval excluding zero indicates that the corresponding no-difference value is outside that interval, but does not by itself establish clinical importance, eliminate bias, or address the consequences of multiple testing.

A p-value measures how unusual data at least as discrepant as those observed would be under a specified null hypothesis and analysis model. It is not the probability that the null hypothesis is true, nor does it quantify the size or importance of an effect. The posted primary comparisons have unadjusted p-values; the registry also posts mixed-model results for selected secondary comparisons. Where sponsor-reported model results are available, they should be distinguished from the simple unadjusted recalculations based on the posted summary statistics.

What is the role of a mixed model?

A mixed-model analysis can account for repeated measurements and model the relationship among measurements from the same participant. It may also use available observations under the model’s assumptions. The registry identifies mixed models for the reported Week 12 change-from-baseline comparisons. However, the specific model terms, covariance structure, handling of missing observations, and assumptions are not reported in the registry record. Therefore, the method label alone does not establish exactly how the analysis handled each design feature or missing value.

The sponsor-reported mixed-model comparison for pregabalin is an LS mean difference of -17.25, with a 95% confidence interval from -25.76 to -8.74 and p < 0.001. For pramipexole 0.25 mg, the posted LS mean difference is -1.07, with a 95% confidence interval from -9.73 to 7.58 and p=0.807. These are the registry’s reported model results. The simple recalculations for the same comparisons are unadjusted approximations from summary statistics and are not identical in every displayed digit. They should not be confused with the sponsor’s model-based analyses.

Why can over-dispersion matter?

For a continuous outcome, variation among participants affects the uncertainty of the group mean and the difference between group means. General statistical principle: if observed variability is greater than a model expects, a model that underestimates that variability can produce confidence intervals that are too narrow and tests that are too optimistic. Conversely, accounting for actual variability is important for appropriate uncertainty estimates. The posted primary standard deviations describe the observed variation, but the registry record does not report a specific over-dispersion assessment or correction.

What do recalculated comparisons and planning illustrations add?

The simple recalculated comparisons use the posted group means, standard deviations and analyzed sample sizes. They are unadjusted and do not recreate the full sponsor analysis. They can help readers see the magnitude and uncertainty of a basic two-group contrast, but they do not incorporate unreported modeling choices or adjustments. Where the registry posts its own analysis, that reported analysis remains distinct from the simplified recalculation.

The planning illustrations translate an observed contrast into hypothetical group sizes under stated assumptions. They are not participants actually enrolled in a future study and are not estimates of the original trial’s planned sample size. Their role is to show how the required group size changes if a design aims to detect a specified fraction of the observed effect under the displayed planning assumptions. Because the calculation starts with observed estimates, it also inherits their uncertainty.

What is not specified?

The registry record does not report the original sample-size justification, the planned significance level for the trial’s primary analysis, a prespecified multiplicity procedure, a full analysis plan, or details of interim analyses. It also does not give complete information about missing-data procedures or the analysis population for every outcome. Those omissions limit the ability to reconstruct the original statistical decisions from the posted summaries alone.

11. Confidence Intervals and Precision

The confidence intervals for the primary baseline comparisons are relatively centered around small mean differences, and all include zero. For pregabalin 300 mg versus placebo, the mean difference is -0.1, with a 95% confidence interval from -1.287 to 1.087. For pramipexole 0.25 mg, the difference is 0.0, with a 95% confidence interval from -1.162 to 1.162. For pramipexole 0.5 mg, the difference is -0.3, with a 95% confidence interval from -1.43 to 0.830. These intervals describe uncertainty around baseline group differences, not uncertainty around a treatment-induced change.

The intervals span values on both sides of zero, so the data are compatible with a modest baseline difference in either direction as well as no difference. Their width is important: a point estimate alone can make an uncertain result appear more definitive than it is. The intervals do not establish equivalence, because no equivalence margin is reported. They also do not speak to clinical importance without a relevant threshold, which is not reported in the registry record.

For the selected Week 12 change-from-baseline outcome, the sponsor-reported mixed-model interval for pregabalin does not include zero, while the reported interval for pramipexole 0.25 mg does include zero. Those are model-based estimates for a different outcome and timeframe from the primary baseline comparisons. They should not be blended with the baseline intervals as if they answered the same question.

Precision depends on both the estimated variability and the number of participants with data for the outcome. The posted analyzed counts are not identical across endpoints or groups, and the registry record does not fully explain the missing observations or their handling. Thus, the displayed intervals are best interpreted as precision under each stated analysis, not as a complete account of uncertainty from missing data, model choice or multiple testing.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations, not the original trial’s design calculations. The posted continuous-outcome values are participants per arm, with separate columns for planning for 80% power and planning for 90% power. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each illustration uses the stated fraction of the observed effect as the effect to detect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

In plain language, power is the chance that a study designed under stated assumptions will detect an effect of the size targeted, if that effect is the true one and the assumptions hold. The 80% column gives the planned number per arm under an 80% power target; the 90% column gives the number per arm under a 90% target. A higher power target generally requires more participants under otherwise identical assumptions. The figures are for each arm, not the combined total.

The rows planning for 100%, 75% and 50% of the observed effect show how the hypothetical target changes. A smaller effect is harder to distinguish from random variation, so it requires more participants per arm under the same design assumptions. This relationship is especially consequential when the observed effect is small, since the resulting planning figures can become very large.

These values are not observed power. They are hypothetical planning calculations based on the observed contrast and stated assumptions, not evidence about the probability that the completed trial detected an effect or about the adequacy of its original design. The registry record does not report the trial’s own sample-size justification. The planning curve should be read as a sensitivity display: as the target effect becomes smaller, the corresponding required group size rises.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.100; pooled standard deviation σ = 5.657.
2. n = 2 × (1.96 + 0.842)² × 5.657² / -0.100² = 50,227.9, rounded up to 50,228 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
delta <- -0.0999999999999979                      # observed difference in means
sigma <- 5.65657781900668                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(806026)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 50,228 (80% power), 67,241 (90% power)
 75% of observed effect: n per arm = 89,295 (80% power), 119,540 (90% power)
 50% of observed effect: n per arm = 200,912 (80% power), 268,964 (90% power)
power.t.test: 50228.9 
Simulated power at n = 50,228 per arm: 0.798 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The record lists 22 outcome measures and 17 analyses, including multiple clinical and sleep measures and more than one treatment comparison. Each additional test creates another opportunity for an apparently notable result to arise by chance, even when the underlying effects are absent. This is the general statistical reason that unadjusted p-values from a collection of secondary outcomes deserve caution. An adjustment or prespecified testing hierarchy can control how evidence is evaluated across several hypotheses, but whether such a strategy was used is not reported in the registry record.

The registry labels selected p-values as unadjusted and posts mixed-model results for two Week 12 change-from-baseline comparisons. It does not report a family-wise error procedure, false-discovery approach, endpoint hierarchy, or a distinction between confirmatory and exploratory secondary analyses. Consequently, the posted nominal results should not be interpreted as if the multiplicity question had been resolved. The record also does not report whether interim analyses occurred or whether they affected testing decisions.

The primary-outcome population description states that it included randomized participants who took at least one dose and had at least one post-randomization efficacy assessment on any efficacy scale. This is the registry’s definition for the stated ITT population, but it is narrower than every randomized participant because it includes medication exposure and an efficacy assessment requirements. The posted analysis counts also vary by outcome. The registry record does not report a complete accounting of participants with missing outcome data, reasons for missingness, or the method used to handle missingness for every endpoint.

Missing data can affect both the representativeness of the analyzed participants and the precision of estimates. General statistical principle: a model-based approach may use incomplete repeated measurements under assumptions about the missing-data process, but that does not remove the need to state and examine those assumptions. The mixed-model label alone is not enough to determine how missing observations were handled. Sensitivity analyses, imputation details, and a full analysis-population description for all outcomes are not reported in the registry record. These gaps limit independent assessment of robustness.

15. 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: cholecystitis acute (1.7%), breast cancer (1.7%), cerebrovascular accident (1.7%), multiple sclerosis (1.7%), suicidal ideation (1.7%).

The registry lists serious adverse event counts for six groups, with the number at risk and the number affected shown separately for each group. For the four continuing treatment groups, serious events were reported for 9 of 182 participants in the pregabalin 300 mg group, 12 of 178 in the pramipexole 0.25 mg group, 9 of 180 in the pramipexole 0.5 mg group, and 5 of 59 in the placebo-to-pregabalin group. The placebo-to-pramipexole 0.25 mg group had 2 of 59 affected, and the placebo-to-pramipexole 0.5 mg group had 0 of 61 affected.

These are counts in the registry’s safety groups, not comparative estimates adjusted for exposure time or other factors. The number at risk differs across groups, and the registry record does not provide exposure-adjusted rates in the registry record. The listed serious terms are acute cholecystitis, breast cancer, cerebrovascular accident, multiple sclerosis, suicidal ideation and withdrawal syndrome, each reported as 1.7%. The posted summary does not specify an arm attribution for each listed term. Death counts are not reported in the registry record. These figures describe recorded events and are not, by themselves, evidence that a treatment caused an event or that risk differs between groups.

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

The primary results answer a narrow descriptive question: what were the mean baseline IRLS scores among the analyzed participants in each named group? Those means are close, and the unadjusted confidence intervals for each group comparison include zero. Because the endpoint is recorded at baseline, these comparisons do not estimate how much symptoms changed during treatment. They also do not establish that groups were equivalent; the registry reports no equivalence margin or equivalence analysis.

The study’s stated purpose concerns efficacy and tolerability over as long as 12 months, and the record includes secondary sleep measures at baseline and Week 12. The posted Week 12 change-from-baseline analysis offers some treatment-comparison information for one sleep outcome, including sponsor-reported mixed-model estimates. Those results remain secondary, and the registry record does not report a multiplicity strategy. They should therefore be read as endpoint-specific results, not as a general conclusion about the full treatment period or all outcomes.

A confidence interval indicates the range of estimates compatible with the analysis assumptions; it does not define clinical importance. No threshold for a clinically meaningful difference is reported in the registry record. Likewise, a p-value does not measure the size of an effect, the probability that a treatment is effective, or the probability that an observed result will recur.

The safety counts identify serious adverse events recorded in the listed groups, but they do not establish causation. The denominators vary, and the posted figures do not offer exposure-adjusted comparisons. Taken together, the registry record supports a careful description of baseline symptom scores, selected sleep outcomes and recorded serious events. It does not, on the primary outcome results alone, establish a treatment effect. The full original statistical plan, details of missing-data handling and multiplicity procedures are not reported in the registry record, so broader conclusions should not be inferred from the posted summaries.

17. Why This Trial Matters Statistically

This trial is statistically instructive because the label primary outcome and the reported timeframe need to be considered together. The endpoint is a validated clinical scale with a clear interpretation, but the posted primary result is a baseline mean. A well-known measure cannot answer a treatment-change question when the reported measurement is at baseline. Reading the endpoint definition alongside its timeframe prevents a descriptive group comparison from being mistaken for an efficacy estimate.

The record also illustrates why point estimates and uncertainty should be considered together. The primary mean differences are small, but the confidence intervals still express a range of baseline differences compatible with the data. A p-value alone would conceal that range and would not provide evidence of equivalence. The distinction between standard deviations, which describe participant variability, and standard errors, which describe estimate precision, is also important in interpreting the different posted outcomes.

Another useful lesson is the separation between sponsor-reported model results and simple unadjusted recalculations. For selected Week 12 results, the registry provides mixed-model comparisons, while the basic recalculations use summary statistics. They answer related but not identical statistical questions and rely on different information. Clear labeling helps prevent an approximate two-group calculation from being treated as a reconstruction of the original analysis.

Finally, the many secondary measures make multiplicity and missing-data reporting consequential. A pattern across outcomes is more informative than an isolated nominal result, but the record does not report a multiplicity procedure or complete missing-data details. The sample-size illustrations add a separate planning lesson: detectable effect size, target power and planned group size are linked, while those illustrations do not reveal the original design rationale. Together, these features show why registry interpretation depends on endpoint, timing, analysis method, uncertainty and reporting completeness.

18. Limitations

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

The principal limitation for interpreting efficacy is that the posted primary endpoint is explicitly at baseline. It does not provide a primary treatment comparison over time, despite the study’s stated interest in treatment for up to 12 months. The selected secondary outcomes include Week 12 information, but they do not replace a later primary endpoint result.

The record lists six arm descriptions, but the posted primary results cover four named groups. The arm descriptions are blank, and details of placebo-to-treatment sequences are not reported in the registry record. This makes it difficult to reconstruct the complete treatment structure and the relationship between all safety groups and efficacy analyses from the posted descriptions alone.

Outcome-specific analyzed counts vary. The registry provides an ITT population description, but the available record does not give a complete disposition of participants by outcome, full reasons for missingness, or the missing-data approach for every analysis. The mixed-model method is named for selected secondary outcomes, but model specifications and assumptions are not reported. The original sample-size justification and full statistical analysis plan are also not reported.

The record includes multiple outcome measures and analyses, while adjustment for multiple comparisons is not reported. This limits the strength of interpretation for isolated secondary p-values. The serious adverse event listing gives counts and group denominators, but not exposure-adjusted comparisons; death counts are not reported in the registry record. These limitations concern reporting and interpretation and do not, by themselves, establish that an analysis was invalid or that an event was caused by treatment.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Long Term Study Of Pregabalin In Idiopathic Restless Legs Syndrome Patients — NCT00806026.
• Registry record last updated 2021-01-26; status last verified 2012-08.
• Results first posted 2012-09-27.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT00806026 is a completed, randomized, double-blind, parallel-group phase 3 study titled Long Term Study Of Pregabalin In Idiopathic Restless Legs Syndrome Patients. The registry describes an enrollment of 731 and a study purpose of investigating pregabalin efficacy and tolerability for up to 12 months. The primary outcome is baseline mean IRLS score. Posted baseline means are similar across pregabalin 300 mg, both pramipexole doses and placebo, and the unadjusted comparison intervals include zero.

The registry also posts selected sleep outcomes, including Week 12 change from baseline in subjective waking after sleep onset, with sponsor-reported mixed-model comparisons for pregabalin and pramipexole 0.25 mg. The primary baseline endpoint does not itself measure treatment-related change. Multiplicity procedures, the original sample-size rationale, and complete missing-data details are not reported in the registry record. Serious adverse event counts are listed by group; death counts are not reported in the registry record.