Placebo-controlled Safety and Efficacy Study of Pregabalin in Subjects With Post-traumatic Peripheral Neuropathic Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Placebo-controlled Safety and Efficacy Study of Pregabalin in Subjects With Post-traumatic Peripheral Neuropathic Pain (NCT01701362), a randomized phase 3 study. The primary outcome is Baseline Mean Pain Score.

2. Clinical Question

The trial's broader clinical question was whether pregabalin differed from placebo for people experiencing neuropathic pain after peripheral nerve trauma. The registry's examples of possible causes include motor vehicle accident, fall, sports injury, joint replacement, hernia repair, thoracotomy, mastectomy, burns, and crush injury. These examples describe the range noted in the record, not necessarily a complete eligibility list.

For statistical interpretation, it matters that the named primary outcome is a baseline pain diary score on an 11-point numeric rating scale. Participants rated pain during the past 24 hours, from 0 for no pain to 10 for worst possible pain. A comparison of baseline group means can describe the groups but does not, by itself, answer whether pain changed differently during follow-up. The Week 15 results posted for pain severity and pain interference are secondary outcomes and should be read as such.

3. Trial Design

This was a Phase 3, randomized, double-blind, parallel-group, placebo-controlled study of pregabalin in subjects with post-traumatic peripheral neuropathic pain. The registry lists enrollment of 542 and status as completed. The recorded study start is 2012-10, and primary completion is recorded as 2015-08. The sponsor is listed as Pfizer's Upjohn, which merged with Mylan to form Viatris Inc.

Participants were assigned to pregabalin or placebo. The official title identifies pregabalin as twice daily, but the registry record does not report the dose, treatment duration, adherence procedures, or details of how randomization and masking were implemented. Arm descriptions are not populated. The record names an Intent to Treat population for the primary outcome: randomized participants who took at least one dose of study drug.

The posted baseline primary outcome includes 274 participants in the pregabalin group and 265 in the placebo group. The Week 15 pain severity result uses 258 and 246 participants, respectively; the Week 15 pain interference result uses 274 and 265. These outcome-specific counts should be read as the numbers contributing to each posted measure, not as evidence about why any participant was not included in a particular analysis. Reasons for differences in outcome counts are not reported in the registry record.

The registry lists 12 outcome measures and 66 analyses. Ten secondary outcomes are posted, including patient global impression, sleep interference, pain severity and interference, quality of life, and sleep-scale measures. The available results do not include every listed outcome. The study's original sample-size rationale, intended analysis hierarchy, interim-analysis plan, and prespecified 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.

Before assignment: Participants had clinic visits at screening, randomization, and during the treatment period, and a phone contact for follow-up after the last taper dose. All the eligible participants were randomly assigned (1:1) to 15 weeks of treatment with Pregabalin or Placebo.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to Treat (ITT) population: all randomized participants who took at least one dose of study drug

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Baseline Mean Pain Score, measured over Baseline.

The primary outcome is the baseline mean pain score, defined from the daily pain diary. Participants described their pain during the past 24 hours using an 11-point numeric rating scale, with 0 meaning no pain and 10 meaning worst possible pain. The registry describes the reported measure as a mean and specifies standard deviation as its dispersion measure. The named analysis population is the Intent to Treat population: randomized participants who took at least one dose of study drug.

A mean is useful for describing the central level of a continuous measure across participants. The standard deviation describes how spread out individual scores are around that mean. These summaries provide context for the groups' starting pain scores and can help readers assess their baseline distributions.

For an efficacy question about treatment, a baseline measurement alone is not a measure of change during treatment. It does not show whether pain subsequently changed, nor whether any change differed between groups. The registry lists Week 15 changes in pain severity and pain interference as secondary outcomes, but the posted primary result remains the baseline score. The reason this baseline measure was designated primary, and its role in the planned efficacy analysis, are not reported in the registry record.

7. Results Posted in the Registry

• Pregabalin: mean 6.41 versus 6.54 on control; difference -0.13 (95% CI -0.35 to 0.09), standardized effect d = -0.10; z-test p = 0.246.

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.

Change From Baseline in Pain Severity Index (Brief Pain Inventory-short Form [BPI-sf])

• 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: mean -2.40 versus -1.95 on control; difference -0.45 (95% CI -0.81 to -0.09), standardized effect d = -0.22; z-test p = 0.014.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Pregabalin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Pain Interference Index (BPI-sf)

• 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: mean -1.72 versus -1.33 on control; difference -0.39 (95% CI -0.75 to -0.03), standardized effect d = -0.18; z-test p = 0.034.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Pregabalin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results cover selected measures of pain and other experiences, while the registry lists a broader set that includes sleep, quality of life, and patient global impression. The two posted Week 15 pain outcomes show negative changes in both groups, with numerically more negative changes in the pregabalin group. Their registry-reported ANCOVA contrasts favor lower numerical change values for pregabalin relative to placebo. The baseline primary outcome, by contrast, describes starting pain scores and is not a treatment-change result.

This makes the secondary findings relevant to the study's efficacy question, but they do not convert the baseline primary result into a follow-up treatment comparison. They also do not establish a consistent pattern across every registered outcome: results for all listed secondary measures are not posted in the record. The relationship between pain scores, sleep, quality of life, and participants' overall impressions cannot be fully assessed from the subset of results available.

Unadjusted secondary findings generally carry less weight when many outcomes or analyses are examined. Each additional analysis creates more opportunity for a result to appear notable by chance. The registry lists 66 analyses, but a multiplicity procedure or prespecified hierarchy is not reported in the registry record. Consequently, the individual secondary p-values should not be read as if they arose from a single isolated test with no other analyses.

The registry's own ANCOVA estimates are the appropriate posted inferential results for the two Week 15 outcomes, while the simple unadjusted recalculations are supplementary checks based on summary statistics. Neither the numerical direction nor a confidence interval alone addresses whether an outcome difference is important to participants. The record does not report a clinical-importance threshold for these scales. Taken together, the secondary results offer outcome-specific evidence, with limited interpretive weight because the full outcome set and multiplicity context are unavailable.

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

• Patient Global Impression of Change (PGIC) at Week 15
• Change From Baseline in Overall Weekly Mean Sleep Interference Score (SIRS)
• Change From Baseline in Pain Severity Index (Brief Pain Inventory-short Form [BPI-sf])
• Change From Baseline in Pain Interference Index (BPI-sf)
• Change From Baseline to Endpoint in Quality of Life Using EuroQol (EQ-5D) Health State Profile Scores
• Baseline Scores in the Medical Outcomes Study Sleep Scale (MOS-SS) - Sub-domain Score.
• Mean Change From Baseline in the Medical Outcomes Study Sleep Scale (MOS-SS) - Sub-domain Score.
• Percentage of Participants in MOS-SS With Optimal Sleep Status.

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean describe? A mean is the arithmetic average of a continuous measurement across the participants included in the analysis. In this trial, the primary result reports mean pain diary scores at baseline. The standard deviation describes how much individual scores vary around that average. Means offer a compact summary, but they do not show the full distribution or whether participants' experiences were similar.

What is a mean difference? A mean difference expresses the contrast between two group means. The comparisons use pregabalin minus placebo, so negative values indicate that the pregabalin group has the lower numerical value for the measure as coded. For the baseline outcome, the contrast is based on the two group means. For the Week 15 outcomes, the registry also reports least-squares means, which are model-based group estimates. A contrast is an estimate, not a guarantee that the same difference would occur in another study.

What is a least-squares mean? A least-squares mean is an estimated group mean from a statistical model. Unlike a raw arithmetic average, it can account for other variables included in that model. The posted Week 15 analyses are identified as ANCOVA, a general approach that compares outcomes while adjusting for covariates. The specific covariates and other implementation details are not reported in the registry record. It is therefore not possible to reconstruct the reported model or determine which baseline factors it included from the results alone.

How should standard errors be read? The Week 15 outcomes report standard errors for the least-squares means. A standard error describes the precision of an estimated mean, rather than the spread of individual participant measurements. In general, a smaller standard error indicates a more precisely estimated mean, all else equal. It should not be interpreted as the same quantity as a standard deviation. The recalculated comparison uses posted summaries and is not a substitute for the trial's ANCOVA model.

What does a confidence interval convey? A confidence interval gives a range of estimates compatible with the data and the statistical method, under the method's assumptions. It displays uncertainty more fully than a single estimate. If an interval for a group difference includes zero, the data are compatible with no difference as well as with differences in either direction. If it excludes zero, that indicates the interval does not include a zero contrast under the stated analysis; it does not establish clinical importance, eliminate bias, or account for unreported multiplicity procedures.

What does a p-value convey? A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be, if that hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The registry includes unadjusted recalculated p-values as well as the p-values from its own reported ANCOVA analyses for the posted Week 15 outcomes. The ANCOVA results are the sponsor's reported analyses; the recalculations are simple unadjusted comparisons from posted summary statistics.

Why does over-dispersion matter in general? In general, over-dispersion occurs when observed variability is greater than a statistical model expects. If a model underestimates variability, standard errors may be too small and inferential results may appear more precise than warranted. This is a general statistical consideration, not a finding reported for this trial. The registry does not report an over-dispersion assessment or a method specific to such an issue.

How do the planning illustrations work? The sample-size illustrations use the observed effect as a reference and show the participants per arm associated with detecting stated fractions of that effect under specified assumptions. They are hypothetical planning calculations, not the trial's original sample-size rationale and not a description of observed power. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The original design assumptions are not reported in the registry record.

Statistical interpretation also depends on decisions not fully documented in the registry record. The analysis plan, handling of missing outcome data, covariate selection, and multiplicity strategy are not reported. These gaps limit how completely a reader can assess the posted estimates and their uncertainty. General statistical explanations describe concepts; they do not establish which procedures were used beyond those explicitly identified in the registry.

11. Confidence Intervals and Precision

The baseline comparison is estimated from the posted group means of 6.41 and 6.54. Its unadjusted difference is -0.13, with an unadjusted p-value of 0.246. The recalculated confidence interval extends to both sides of zero. This means the baseline summaries do not pin down a directional group difference with high precision. It is also important that this is a baseline comparison, not an estimate of a treatment-related change.

For Week 15 pain severity, the registry's ANCOVA estimate is -0.46, with a 95% confidence interval from -0.77 to -0.14. For pain interference, the ANCOVA estimate is -0.38, with a 95% confidence interval from -0.70 to -0.07. Both intervals lie below zero for the stated contrast of pregabalin minus placebo. Their width reflects remaining uncertainty about the magnitude of the estimated differences. The intervals do not indicate whether the differences meet a threshold of importance to participants; such a threshold is not reported in the registry record.

Confidence intervals are not guarantees that the true effect lies within a particular range, nor do they incorporate every possible source of uncertainty. They depend on the model and assumptions used in the analysis. The registry identifies ANCOVA for the Week 15 analyses but does not report all model details. The interval for a simple unadjusted recalculation and the interval for the registry's ANCOVA analysis need not be identical because they arise from different analyses.

Precision should also be considered alongside outcome availability and multiplicity. The record lists more outcome measures and analyses than the secondary results posted, and does not report a multiplicity strategy. Confidence intervals for individual outcomes do not resolve the uncertainty created by examining multiple outcomes. These estimates describe the precision of the reported contrasts under their analyses, rather than providing a complete uncertainty assessment for every possible study question.

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 participants per arm, not total events. They are planning illustrations based on the observed effect, not the study's original design calculation. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% column gives the corresponding illustrative number per arm for a 90% chance. Power is a design property calculated under assumptions; it is not the probability that the trial's conclusion is correct. These figures are not observed power.

Read each row as a distinct planning scenario: one uses 100% of the observed effect, another uses 75% of the observed effect, and another uses 50% of the observed effect. Smaller target effects require more participants per arm to reach the same target power, all else equal. For example, the listed requirements rise as the planning target moves from the full observed effect to a smaller fraction. This is a general consequence of needing more information to distinguish a smaller contrast from random variation.

The values are conditional on the stated assumptions and should not be treated as a recommendation for a future study. The registry does not report the original sample-size justification, the effect assumed when the trial was designed, or whether the original plan used these assumptions. The planning calculations also do not establish that the observed trial had a particular probability of detecting its actual effect.

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 = -0.130; pooled standard deviation σ = 1.300.
2. n = 2 × (1.96 + 0.842)² × 1.300² / -0.130² = 1,569.8, rounded up to 1,570 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 <- -0.13                      # observed difference in means
sigma <- 1.3                     # 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(1701362)
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 = 1,570 (80% power), 2,102 (90% power)
 75% of observed effect: n per arm = 2,791 (80% power), 3,736 (90% power)
 50% of observed effect: n per arm = 6,280 (80% power), 8,406 (90% power)
power.t.test: 1570.7 
Simulated power at n = 1,570 per arm: 0.803 (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

Multiplicity arises when a study evaluates several outcomes, time points, comparisons, or analyses. Even when each individual analysis uses a conventional statistical method, examining many results increases the chance that some will look unusual by chance alone. Here the registry lists 12 outcome measures and 66 analyses, and 10 secondary outcomes are posted. The registry record does not report whether the study used a multiplicity adjustment, a hierarchical testing procedure, or another strategy to control interpretation across analyses.

Without that information, the posted Week 15 secondary p-values should be treated as outcome-specific results rather than definitive evidence across the full set of outcomes. The registry's reported ANCOVA analyses remain more relevant than simple unadjusted recalculations for those endpoints, but use of ANCOVA does not, by itself, resolve multiplicity. No prespecified ordering of primary and secondary hypotheses is reported beyond the registry's outcome labels.

Missing-data handling is also not reported in the registry record. The primary population is defined as randomized participants who took at least one dose, but that population label does not explain how missing diary entries or missing Week 15 outcomes were handled. The record does not state whether the analyses used imputation, a likelihood-based approach, observed cases, or another method. Reasons for the outcome-specific participant counts are not reported either. These omissions matter because different approaches to unavailable measurements can affect estimates and their uncertainty.

The registry describes the primary endpoint as a baseline mean pain score, while the posted post-baseline pain results are secondary. A full analysis plan could clarify how this outcome structure was intended to support the clinical question, but that plan is not reported in the registry record. Interim analyses, stopping rules, subgroup analyses, and the detailed covariates used in ANCOVA are also not reported. These are reporting gaps, not evidence that a particular procedure was or was not used.

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: haemorrhoids (0.4%), concussion (0.4%), overdose (0.4%), post procedural discharge (0.4%), lumbar spinal stenosis (0.4%).

The registry lists serious adverse events for 2 participants among 274 at risk in the pregabalin group and 7 among 265 at risk in the placebo group. It also lists other adverse events for 75 among 274 at risk with pregabalin and 33 among 265 at risk with placebo. These are separate registry categories; the record does not explain whether or how participants could contribute to more than one category. Counts should be interpreted as the posted group figures, not as a complete description of event timing, duration, severity, or relationship to treatment.

The serious adverse event terms listed with the highest reported percentages each have a value of 0.4%: haemorrhoids, concussion, overdose, post procedural discharge, lumbar spinal stenosis, and major depression. The record does not provide further context for these terms in the data summarized. Death counts are not reported in the registry record. Safety comparisons require caution because the counts alone do not establish cause, risk difference, or the full clinical context of events.

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

The posted results support a limited statistical description of this study. The baseline pain means are close in numerical terms, and the unadjusted baseline comparison is imprecise in the sense that its confidence interval spans zero. Because baseline pain is not a follow-up change measure, this comparison does not establish whether pain improved, worsened, or changed differently between groups during the study.

The two available Week 15 pain outcomes show numerically more negative changes in the pregabalin group than in the placebo group. The registry reports ANCOVA contrasts and confidence intervals for both. Those results describe the selected secondary outcomes under the reported analyses; they do not by themselves establish the clinical importance of the differences or resolve the impact of multiple analyses and unavailable results. The registry record does not provide a threshold for a meaningful change on either scale.

These results do not establish that every person in either group experienced the group-average change. A mean summarizes participants and can conceal variation in individual outcomes. Nor do the posted comparisons establish why an observed difference occurred or whether it would generalize to people outside the study population. The registry does not report enough detail to assess all eligibility criteria, missing-data procedures, or model specifications.

Safety counts are descriptive registry entries. They do not, by themselves, show that an event was caused by a study treatment, and the death information is not reported in the registry record. The available figures also cannot substitute for a complete safety assessment that considers event descriptions and clinical context.

Overall, the record presents baseline pain summaries, selected secondary pain results, and adverse-event counts. It does not provide a complete account of every registered outcome or the full statistical plan. The numbers should be interpreted as the posted evidence with those limits in view, not as medical advice or a treatment recommendation.

17. Why This Trial Matters Statistically

This trial illustrates why the label and timing of an endpoint matter. A primary outcome described as a baseline mean can characterize the groups at the start of measurement, but it is not itself a treatment-change estimate. Readers need to distinguish that result from the Week 15 secondary outcomes, which compare changes from baseline. Treating both as equivalent efficacy evidence would obscure what each measure can answer.

It also shows why model-based estimates and simple recalculations should not be conflated. The registry reports ANCOVA results for the posted Week 15 outcomes, while unadjusted contrasts can be recalculated from summary values. Those analyses answer related but not identical statistical questions. The trial's own reported analysis takes precedence for interpretation of its modeled outcomes; recalculations are useful as transparent, limited checks rather than replacements for the analysis plan.

The record further highlights the importance of multiplicity and completeness. It lists many analyses but does not report a multiplicity strategy, and only some of the listed secondary outcomes have posted results. A reader therefore cannot treat an individual secondary finding as if it were the only test conducted or infer that unposted outcomes showed a particular pattern.

Finally, the planning illustrations demonstrate that sample-size requirements depend on the size of the effect a study aims to detect. Those illustrations are distinct from the trial's original design rationale, which is not reported. Together, these features make the study a useful example of careful endpoint reading, qualified interpretation of secondary findings, and separation of observed summaries from planning calculations.

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 primary outcome reported is a baseline measure, while the posted Week 15 pain outcomes are secondary. This limits the extent to which the posted primary result answers the study's stated efficacy question. The rationale for selecting baseline mean pain score as the primary outcome and its intended role in the analysis are not reported in the registry record.

Only selected secondary results are posted, despite the registry listing 12 outcome measures and 66 analyses. The record does not report a multiplicity strategy or a hierarchy for interpreting the outcomes. This makes it difficult to place individual secondary findings in the context of all analyses conducted. Results for the other listed outcomes cannot be inferred from the results that are available.

Important analysis details are absent, including handling of missing data, the covariates in the Week 15 ANCOVA models, and the original sample-size justification. Although the primary population is defined, the record does not explain the outcome-specific participant counts or why they differ across measures. These gaps limit assessment of the analysis assumptions and the possible influence of unavailable measurements.

Intervention details are also sparse: the official title identifies twice-daily pregabalin, but dose and adjustment details are not reported, and arm descriptions are blank. The registry's safety entries do not provide fuller event context, and death counts are not reported. These limitations concern the detail available in the registry record and do not establish that the study lacked procedures or analyses that are not documented there.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Placebo-controlled Safety and Efficacy Study of Pregabalin in Subjects With Post-traumatic Peripheral Neuropathic Pain — NCT01701362.
• Registry record last updated 2021-01-28; status last verified 2017-04.
• Results first posted 2017-06-07.
• 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

The registry describes a completed randomized, double-blind, parallel-group, placebo-controlled Phase 3 study of pregabalin for post-traumatic peripheral neuropathic pain. Enrollment is listed as 542. The posted primary outcome is baseline mean pain diary score, and selected Week 15 secondary results report changes in pain severity and pain interference.

The baseline group means are 6.41 for pregabalin and 6.54 for placebo. For the posted Week 15 secondary pain outcomes, the registry reports ANCOVA contrasts with 95% confidence intervals that exclude zero. These results are secondary, and the record does not report a multiplicity strategy or complete results for all listed outcomes.

The registry also lists serious and other adverse-event counts. Missing-data procedures, the trial's original sample-size rationale, and several analysis details are not reported in the registry record. Interpretation should distinguish baseline description from post-baseline outcomes and consider the limits of the posted results.