Study Evaluating the Abuse Potential of NEURONTIN® in Healthy Non-drug Dependent, Recreational Opioid Users: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study Evaluating the Abuse Potential of NEURONTIN® in Healthy Non-drug Dependent, Recreational Opioid Users (NCT05319756), a randomized phase 4 study. The primary outcome is Bipolar Visual Analog Scale (VAS) for "Drug Liking" Maximum Effect (Emax)..

2. Clinical Question

The study title and listed outcomes frame the question around whether participants like or dislike the drug effect, and how that rating changes over time. The primary endpoint was the maximum Drug Liking score after treatment. Secondary outcomes include other summaries of the same rating, such as time to maximum effect and area under the effect curve, as well as a measure of “High.” Those outcomes provide different views of participants’ reported experiences, rather than independent measures of clinical benefit.

The design included gabapentin at two doses, oxycodone alone, each gabapentin dose combined with oxycodone, and placebo. The crossover structure means the treatment comparisons are made across treatment periods within a study that exposes participants to the different conditions. The posted arm summaries and the sponsor’s mixed models are different kinds of summaries; the latter are the sponsor’s reported analyses. The analysis population and the registry’s exclusions are important context when considering how broadly the results can be interpreted.

3. Trial Design

This completed phase 4 study was randomized, quadruple-masked, placebo- and active-controlled, and used a crossover model. The brief description identifies a single-dose, six-treatment, six-period Williams square design. Its six treatment conditions were gabapentin 600 mg, gabapentin 1200 mg, oxycodone HCl 20 mg, each gabapentin dose combined with oxycodone HCl 20 mg, and placebo. The study enrolled 54 participants. The registry lists the study start as 2021-04-30 and primary completion as 2021-12-31.

In a crossover study, a participant receives more than one treatment condition across different periods. This can make within-participant comparisons possible, but those comparisons depend on the analysis accounting appropriately for the design. The registry identifies mixed models for the sponsor’s posted analyses. Further details of the model specification, including the terms included for period, sequence, or other design features, are not reported in the registry record.

The primary endpoint analysis population was not simply everyone enrolled. It was a modified completer population that included participants completing all six periods, while excluding participants identified during data review as having similar maximum Drug Liking scores for all six treatments or high placebo responses. The arm summaries report 42 participants for each treatment condition. The registry does not explain the difference between enrollment and the number in these endpoint summaries, so the reasons for that difference are not reported in the registry record.

The study focused on healthy, non-drug-dependent recreational opioid users, not a broad clinical population. Its single-dose conditions and selected analysis population define the scope of the observations. The original design’s sample-size rationale, any planned interim analyses, and the full statistical analysis plan are not reported in the registry record. The posted information therefore allows a description of the design and results, but not a complete reconstruction of all design decisions.

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: Subjects were entered into a Qualification phase involving a naloxone challenge test (to exclude subjects who were opioid dependent) and a drug discrimination test (to confirm they can tell the difference between oxycodone and placebo). Only subjects who passed the tests in the Qualification phase were randomized into the Treatment phase where they received the 6 different single dose study treatments, each separated by a washout of at least 4 days, in the order specified for Sequences 1-6 below

Overall Study

Analysis population for the primary outcome, as defined in the registry: The analysis population was the modified completer population which included subjects who completed all 6 treatment periods but excluded those identified during data review as having maximum Drug Liking scores that were similar for all 6 treatments or who had high placebo responses

5. Baseline Characteristics

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

Population: The randomized population included all participants who were randomized to a treatment sequence in the Treatment Phase.

6. Primary Endpoint

The registry lists the primary outcome as Bipolar Visual Analog Scale (VAS) for "Drug Liking" Maximum Effect (Emax)., measured over up to 48 hours after treatments.

The primary endpoint was the maximum effect, or Emax, on a bipolar visual analog scale for “Drug Liking,” measured up to 48 hours after treatment. Participants rated how much they liked or disliked the drug effect at the moment they were asked, “at this moment, my liking this drug is.” The scale ran from 0 mm, meaning “Strong Disliking,” through 50 mm, meaning “Neither Like nor Dislike,” to 100 mm, meaning “Strong Liking.” The posted summaries give means and standard errors.

As a general statistical explanation, a maximum-effect measure captures the highest recorded rating during the observation window. It can summarize the peak response while not describing its duration or the pattern of ratings at every assessment. The registry also lists time-to-maximum and area-under-the-effect-curve outcomes, which address timing and accumulated ratings over time in different ways.

Drug Liking is used because the study’s stated purpose concerns abuse potential, and the rating directly records participants’ subjective liking or disliking. It is not a measure of a clinical condition improving, nor does a group mean reveal how every participant responded. The endpoint is self-reported, and interpretation depends on the study population, the treatment conditions, the analysis population, and the analysis method. The registry’s definition of the modified completer population is therefore relevant to what the posted mean represents.

7. Results Posted in the Registry

• Oxycodone HCl 20 mg Single Dose: mean 87.40 versus 54.89 on control; difference 32.51 (95% CI 25.06 to 39.96), standardized effect d = 1.87; z-test p = <0.001.
• Gabapentin 600 mg Single Dose: mean 57.89 versus 54.89 on control; difference 3.00 (95% CI -4.42 to 10.42), standardized effect d = 0.17; z-test p = 0.428.
• Gabapentin 1200 mg Single Dose: mean 63.62 versus 54.89 on control; difference 8.73 (95% CI 0.99 to 16.47), standardized effect d = 0.48; z-test p = 0.027.
• Gabapentin 600 mg and Oxycodone HCl 20 mg: mean 88.43 versus 54.89 on control; difference 33.54 (95% CI 25.99 to 41.09), standardized effect d = 1.90; z-test p = <0.001.

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.

Bipolar VAS for "Drug Liking": Area Under the Effect Curve From Time 0 to the Last Available Data (AUEClast)

• 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:
  • Oxycodone HCl 20 mg Single Dose: mean 2,661 versus 2,394 on control; difference 267.22 (95% CI 58.29 to 476.15), standardized effect d = 0.55; z-test p = 0.012.
  • Gabapentin 600 mg Single Dose: mean 2,422 versus 2,394 on control; difference 28.16 (95% CI -183.22 to 239.54), standardized effect d = 0.06; z-test p = 0.794.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Oxycodone HCl 20 mg Single Dose 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 Gabapentin 600 mg Single Dose and the control. The interval gives the range of effects that remain compatible with the data.

Bipolar VAS for "Drug Liking": Area Under the Effect Curve to 1 Hour (AUEC1)

• 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:
  • Oxycodone HCl 20 mg Single Dose: mean 58.86 versus 50.17 on control; difference 8.69 (95% CI 5.73 to 11.65), standardized effect d = 1.25; z-test p = <0.001.
  • Gabapentin 600 mg Single Dose: mean 51.28 versus 50.17 on control; difference 1.11 (95% CI -1.78 to 4.00), standardized effect d = 0.16; z-test p = 0.452.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Oxycodone HCl 20 mg Single Dose 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 Gabapentin 600 mg Single Dose and the control. The interval gives the range of effects that remain compatible with the data.

Bipolar VAS for "Drug Liking": Area Under the Effect Curve to 2 Hours (AUEC2)

• 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:
  • Oxycodone HCl 20 mg Single Dose: mean 140.44 versus 102.62 on control; difference 37.82 (95% CI 28.45 to 47.19), standardized effect d = 1.73; z-test p = <0.001.
  • Gabapentin 600 mg Single Dose: mean 105.20 versus 102.62 on control; difference 2.58 (95% CI -6.04 to 11.20), standardized effect d = 0.13; z-test p = 0.557.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Oxycodone HCl 20 mg Single Dose 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 Gabapentin 600 mg Single Dose and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary Drug Liking question across time and related subjective measures. They include time to maximum effect, area-under-the-effect-curve summaries over several windows, and a “High” rating. These measures can add context about the timing or accumulated pattern of reported effects, but they do not measure exactly the same feature as maximum Drug Liking. The secondary tables should therefore be read as complementary descriptions, not as repeated versions of the primary endpoint.

Across the posted area-under-the-curve summaries, the oxycodone-alone and combination conditions tend to have higher mean values than placebo, while gabapentin alone is closer to placebo in the listed summaries. This broad pattern is consistent with the descriptive pattern in the primary endpoint, but it does not establish that every secondary outcome behaves in the same way. The endpoint windows differ, and each result has its own uncertainty. The tables contain the individual posted values and recalculated comparisons; this discussion does not restate those endpoint-by-endpoint results.

The registry lists many outcomes and analyses. When numerous outcomes or comparisons are examined, some results can appear notable by chance even if there is no underlying difference. This is the general multiplicity concern. The registry record does not report whether a multiplicity adjustment was used or how the secondary outcomes were ordered for formal testing. In addition, the recalculated secondary comparisons are unadjusted. They should consequently carry less weight than a prespecified primary analysis and should be treated as supportive, exploratory descriptions rather than independent confirmation.

The listed outcome “High” is distinct from Drug Liking, and numerical results for it are not reported in the registry record. More generally, a pattern across secondary outcomes can help describe the results but cannot resolve limitations in the analysis population, the crossover model details, or the lack of reported multiplicity procedures. The sponsor’s formal analyses and the endpoint-specific tables remain the appropriate sources for interpreting each result.

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

• Bipolar VAS for "Drug Liking" - Time to Maximum Effect (TEmax)
• Bipolar VAS for "Drug Liking": Area Under the Effect Curve From Time 0 to the Last Available Data (AUEClast)
• Bipolar VAS for "Drug Liking": Area Under the Effect Curve to 1 Hour (AUEC1)
• Bipolar VAS for "Drug Liking": Area Under the Effect Curve to 2 Hours (AUEC2)
• Bipolar VAS for "Drug Liking": Area Under the Effect Curve to 3 Hours (AUEC3)
• Bipolar VAS for "Drug Liking": Area Under the Effect Curve to 4 Hours (AUEC4)
• Bipolar VAS for "Drug Liking": Area Under the Effect Curve to 8 Hours (AUEC8)
• Unipolar VAS for "High" - Maximum Effect (Emax)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a score on a 100 mm scale, summarized in the registry as a mean with a standard error. A mean gives a central summary of the recorded scores. A standard error describes uncertainty in the estimated mean, not the spread of individual participant scores. As a general statistical explanation, standard errors are useful for assessing the precision of a group estimate, but they should not be mistaken for the range of individual experiences.

The trial used a crossover design, with participants assigned to treatment sequences and exposed to multiple conditions over six periods. This differs from a parallel-group study in which each participant receives only one assigned condition. General statistical reasoning says that measurements from the same participant may be related; a model that uses the crossover structure can account for features of that design. The registry identifies the sponsor’s approach as mixed models analysis. The specific model terms, covariance structure, treatment of period or sequence, and any carryover assessment are not reported in the registry record.

The calculated comparisons are labelled as recalculated because they are simple, unadjusted comparisons based on the posted arm summaries. They are not the sponsor’s mixed-model estimates. In particular, the unadjusted calculations do not reconstruct the participant-level covariance information of a crossover trial. Their confidence intervals and p-values are consequently descriptive aids rather than substitutes for the sponsor’s formal model. Where the record flags a discrepancy, the sponsor’s own analysis takes precedence.

A confidence interval gives a range of values that are compatible with an estimate under the method’s assumptions. In general, a narrower interval indicates greater precision, while a wider interval indicates less precision. An interval that includes zero for a difference is compatible with no difference under that calculation; an interval that excludes zero is not, by itself, proof of clinical importance. The scale’s interpretation and the analysis design still matter. For sponsor analyses with a bound missing from the registry entry, the unreported bound cannot be inferred from the other information.

The sponsor’s posted analyses include superiority and non-inferiority categories. These ask different questions. A superiority analysis evaluates evidence that one condition has a higher or lower result than another under the specified model. A non-inferiority analysis evaluates whether an effect is not worse than a prespecified margin in a stated direction. General interpretation of a non-inferiority test requires the margin, the direction of the contrast, and the analysis specification. The margin is not reported in the registry record, so the posted non-inferiority entries cannot be fully evaluated from the information.

The registry lists 26 outcome measures and 79 analyses. Several secondary endpoints summarize Drug Liking over a period or to a specified time, and another listed outcome measures “High.” For an area-under-the-effect-curve outcome, larger values reflect more accumulated scale score over the stated observation window; the value is not the same as a peak score. Time to maximum summarizes when the highest effect was observed, while Emax summarizes the peak itself. These measures answer related but distinct questions, and they should not be treated as interchangeable confirmations.

Multiplicity is the general problem that arises when many outcomes, contrasts, or analyses are examined: the chance of at least one apparently unusual result can increase as more tests are conducted. The registry’s primary endpoint and its secondary outcomes are identified, but whether and how the sponsor adjusted for multiple testing is not reported in the registry record. The recalculated p-values are explicitly unadjusted. They should therefore be read cautiously and in the context of the endpoint hierarchy and the sponsor’s reported analyses.

The primary analysis population is a modified completer population, requiring completion of all treatment periods and excluding specified response patterns. That definition can affect which participants contribute to the endpoint summaries and how broadly those summaries apply. The handling of other missing observations, incomplete treatment periods, and missing endpoint values is not reported in the registry record. The results therefore describe the posted analysis population; they do not, on their own, show what the result would have been under another missing-data approach or in all enrolled participants.

The registry also gives a planning illustration based on observed effects. This illustration uses a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and a target effect equal to a stated fraction of the observed effect. Those are assumptions for the illustration, not the reported assumptions behind the trial’s original design. Such calculations describe how a hypothetical two-arm study might be planned under those assumptions; they do not establish what the original investigators planned.

11. Confidence Intervals and Precision

The recalculated intervals show how uncertain the simple unadjusted mean differences are around the posted arm summaries. For oxycodone HCl 20 mg versus placebo, the recalculated difference is 32.51, with a 95% interval from 25.06 to 39.96. For gabapentin 600 mg versus placebo, the estimate is 3.0 and the interval runs from -4.425 to 10.42, spanning zero. For gabapentin 1200 mg versus placebo, the estimate is 8.73 and the interval runs from 0.991 to 16.47. The interval for the 1200 mg recalculation is comparatively close to zero at its lower end, so the estimated difference is less precise about how far the values are from zero than the point estimate alone might suggest.

For the combination conditions, the recalculated intervals are 25.99 to 41.09 for gabapentin 600 mg with oxycodone and 30.54 to 44.02 for gabapentin 1200 mg with oxycodone. These intervals are based on the unadjusted summary-statistic calculations, not the sponsor’s mixed model. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence for formal interpretation. The sponsor reports a 95% interval lower bound of 26.1 for the placebo–oxycodone superiority analysis, but the upper bound is not reported in the registry record.

As a general explanation, an interval describes uncertainty in an estimate under a particular analysis and its assumptions; it is not a range containing a stated proportion of individual scores. Nor does an interval alone determine whether a difference matters in practice. The crossover design, modified completer population, and distinction between sponsor analyses and recalculations all affect interpretation. The full intervals and arm summaries are available in the tables and should be read with those qualifications in mind.

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 section is a planning illustration, not a report of the trial’s original sample-size calculation. For this continuous outcome, the table gives participants per arm, not a total number of events. The calculation assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It uses an effect to detect set at the stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under its assumptions. The 90% power column gives the corresponding planning figure for a 90% chance. These are hypothetical planning targets, not results observed in this study. This is not observed power.

The rows use different fractions of the observed effect. Planning for a smaller effect generally requires more participants, because a smaller signal is harder to distinguish from random variation under a fixed analysis and assumptions. The figures are therefore sensitive to the observed effect used as their starting point. If that effect is imprecisely estimated or does not represent the effect a future study aims to detect, the resulting planning illustration may not be a suitable design target. The table is best read as a set of conditional examples, not as a recommendation about the size of another study.

The illustration also uses a two-arm equal-allocation setup, whereas this trial used a six-treatment crossover design. Its figures do not reproduce the original crossover design or its statistical model. The table’s role is to show how hypothetical sample-size requirements change across the listed effect assumptions and power targets; it does not explain why the study enrolled 54 participants.

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 = 32.510; pooled standard deviation σ = 17.412.
2. n = 2 × (1.96 + 0.842)² × 17.412² / 32.510² = 4.5, rounded up to 5 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 <- 32.51                      # observed difference in means
sigma <- 17.4124562311008                     # 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(5319756)
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 = 5 (80% power), 7 (90% power)
 75% of observed effect: n per arm = 9 (80% power), 11 (90% power)
 50% of observed effect: n per arm = 19 (80% power), 25 (90% power)
power.t.test: 5.6 
Simulated power at n = 5 per arm: 0.736 (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. Analyses Reported by the Sponsor

The sponsor’s analyses use mixed models and are the formal analyses posted in the registry. The recalculated values on this page are simple, unadjusted comparisons of the posted summary statistics. They are not a reanalysis of participant-level crossover data, and the record identifies a discrepancy between them and the sponsor’s analysis. For that reason, the sponsor’s own analysis takes precedence when the results differ.

For the placebo and oxycodone HCl 20 mg superiority comparison, the sponsor reports a mean difference of 32.8, a 95% confidence interval lower bound of 26.1, and p <.0001. The upper confidence bound is not reported in the registry record. The simple recalculation gives a mean difference of 32.51, with a 95% interval from 25.06 to 39.96 and an unadjusted p < 0.001. These figures are similar in broad direction, but they come from different analyses, so they should not be treated as identical estimates or as interchangeable tests.

Other sponsor entries are labelled non-inferiority and include comparisons involving the combination treatments and gabapentin alone. Their hypotheses differ from the simple recalculations against placebo. The registry does not report the non-inferiority margin or full model details, so the p-values and bounds cannot be interpreted as ordinary tests of whether two conditions are the same. The sponsor results should be read in their recorded analysis category, and not replaced by the unadjusted calculations.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a large set of outcomes and analyses, including the primary maximum Drug Liking measure and multiple secondary measures of ratings over time. As a general statistical issue, testing many outcomes or contrasts creates more opportunities for chance findings. A multiplicity procedure can control or describe that issue, but the use and details of any such procedure are not reported in the registry record. The recalculated p-values are unadjusted and should not be read as if they accounted for all outcomes and comparisons.

The registry describes a modified completer population for the primary endpoint. Participants had to complete all six treatment periods, and those identified during data review as having similar maximum Drug Liking scores across all six treatments or high placebo responses were excluded. This rule is part of the stated analysis population definition. It is not possible from the record to assess how the results would change under a different population definition.

Enrollment was 54, while the primary endpoint summaries report 42 participants per treatment condition. The reason for this difference is not reported in the registry record. Because this is a crossover study, the treatment summaries should not be interpreted as if they necessarily represented separate, non-overlapping groups of participants. The registry does not provide enough detail to reconstruct participant flow across periods or determine why particular endpoint observations were unavailable.

The strategy for handling missing endpoint measurements, incomplete periods, or participants who did not complete all treatment conditions is not reported in the registry record. The record also does not describe any sensitivity analyses for missing data. These gaps make it difficult to evaluate whether the posted completer results might differ under alternative assumptions about missingness. They do not invalidate the posted summaries, but they limit what can be concluded about robustness.

The registry identifies mixed models for the sponsor’s reported analyses, but the full model specification is not reported. The handling of treatment period, sequence, within-participant correlation, and any potential carryover is therefore not assessable from the posted description alone. Similarly, a non-inferiority margin is not reported. These omissions matter for interpreting the sponsor’s formal comparisons and reinforce the distinction between those analyses and the unadjusted recalculations.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry’s serious adverse event table reports zero affected participants in every treatment group and zero deaths in every group. The numbers at risk differ by condition, ranging from 51 to 53, as shown in the safety table. These are the posted counts; they should be read with the treatment-specific denominators rather than treated as if every condition had the same number at risk.

The table also reports affected participants for other, non-serious adverse events: 0 for placebo, 4 for oxycodone HCl 20 mg, 0 for gabapentin 600 mg, 2 for gabapentin 1200 mg, 4 for gabapentin 600 mg with oxycodone, and 2 for gabapentin 1200 mg with oxycodone. These counts describe participants affected as recorded in the registry, not the total number of event episodes or their severity. The registry’s listed serious-event terms are empty.

As a general statistical caution, zero observed serious events does not establish that an event cannot occur or that risks are absent. The study was a single-dose study in a selected population, and the table provides counts rather than a detailed account of event types, timing, or individual exposure. These safety figures are descriptive and should not be used as medical advice.

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

This study reports how a selected group of healthy, non-drug-dependent recreational opioid users rated Drug Liking after single-dose treatment conditions. The posted summaries show differences in mean maximum ratings across conditions, and the sponsor’s mixed-model analysis reports a superiority comparison between placebo and oxycodone HCl 20 mg. The results are observations about subjective ratings under this study’s conditions.

They do not establish a clinical benefit for gabapentin or oxycodone, and the endpoint is not a measure of treatment effectiveness for a health condition. The study’s stated focus is abuse potential, but a rating scale is only one type of evidence. These results alone do not establish how people in other populations would respond, how ratings would change with repeated exposure, or what outcomes would occur outside the study setting.

The interpretation also depends on the analysis population. The primary endpoint summaries are based on participants who completed all treatment periods, with specified exclusions for response patterns. The results therefore do not automatically represent all enrolled participants. The crossover design is another reason to distinguish the sponsor’s model-based analyses from simple comparisons of group summaries. The sponsor’s analysis takes precedence where the record flags discrepancies.

The findings should not be reduced to a single p-value. The size and uncertainty of the estimates, the scale’s meaning, the sponsor’s analysis, and the study’s design all matter. Secondary outcomes add descriptions of other aspects of the reported experience, but the registry does not report whether multiplicity was addressed. The posted data can inform a statistical reading of this trial, but they do not support claims beyond the population, treatments, dose conditions, endpoints, and analyses recorded.

18. Why This Trial Matters Statistically

This trial illustrates several important statistical features of clinical research. First, its crossover structure means that the same study includes multiple treatment conditions across periods. That design can produce informative within-participant comparisons, but it also means that simple comparisons of arm summaries are not the same as a model-based analysis of the trial. Here, the registry posts both descriptive summaries and sponsor mixed-model results, and the record identifies a discrepancy between sponsor analyses and recalculations.

Second, the primary endpoint is a subjective continuous rating, summarized by its maximum during the observation window. A peak score conveys one aspect of an experience but not its full timing or duration. The secondary time-to-maximum and area-under-the-curve outcomes illustrate why endpoint choice matters: related measures can describe different features of the same general rating.

Third, the analysis population is a substantive part of the result. Requiring completion of all periods and excluding specified response patterns affects which participants contribute to the primary summaries. The number enrolled and the number in the endpoint summaries are not the same, and the reason for the difference is not reported in the registry record.

Finally, many outcomes and comparisons invite careful attention to multiplicity, prespecification, and uncertainty. The record contains numerous analyses, but multiplicity procedures and the full statistical plan are not reported. The sample-size illustration is also distinct from the trial’s own design rationale. Together, these features show why statistical interpretation should consider the endpoint, design, analysis population, model, and precision—not only the direction of a mean or the threshold of a p-value.

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.

The study’s population is narrowly defined: healthy adult recreational opioid users who were not drug dependent. Results from this group should not be assumed to describe other populations. The conditions were single doses, so the record does not establish how the measured ratings relate to repeated dosing or longer-term exposure.

The primary analysis used a modified completer population. Participants had to complete all six periods, and specified response patterns led to exclusion. This may limit how directly the summaries describe everyone enrolled. Enrollment was 54 and the endpoint summaries report 42 participants per condition, but the reason for that difference is not reported in the registry record.

The sponsor’s analysis is identified as mixed models analysis, but its full specification is not reported. The registry does not provide the terms used to represent period and sequence, the covariance structure, the handling of missing observations, or details of any carryover evaluation. The non-inferiority margin is also not reported, limiting interpretation of those entries. The recalculated comparisons are unadjusted and use posted summary statistics, so they do not reconstruct the sponsor’s participant-level crossover analysis.

The record lists multiple outcomes and analyses, while multiplicity procedures are not reported. This limits confidence in treating secondary findings as confirmatory. The table of sample-size illustrations is based on the observed effect and stated hypothetical assumptions; it is not the original trial’s sample-size justification. Finally, the primary measure is a self-reported rating. It captures participants’ stated liking at assessments, not a complete account of behavior or clinical consequences.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study Evaluating the Abuse Potential of NEURONTIN® in Healthy Non-drug Dependent, Recreational Opioid Users — NCT05319756.
• Registry record last updated 2023-08-14; status last verified 2023-07.
• Results first posted 2023-08-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

This completed phase 4 randomized, quadruple-masked, placebo- and active-controlled crossover study evaluated six single-dose conditions in healthy, non-drug-dependent recreational opioid users. The primary endpoint was maximum Drug Liking on a 100 mm visual analog scale, assessed up to 48 hours after treatment. Enrollment was 54, and the primary endpoint summaries report 42 participants per condition.

The posted means vary across placebo, oxycodone, gabapentin, and combination conditions. The sponsor reports mixed-model superiority and non-inferiority analyses, while the simple recalculations are unadjusted; the sponsor’s analysis takes precedence where the record flags a discrepancy. The full model details, multiplicity procedures, missing-data methods, and original sample-size rationale are not reported in the registry record.

The findings describe subjective ratings in the stated population and study conditions. They should be interpreted alongside the crossover design, modified completer population, uncertainty in the estimates, and the distinction between primary and secondary analyses.