Oral LAT8881 in Neuropathic Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Oral LAT8881 in Neuropathic Pain (NCT03865953), a randomized phase 2 study. The primary outcome is Absolute Change in Mean Pain Score, Using an 11 Point Numeric Pain Rating Scale (NPRS).

2. Clinical Question

3. Trial Design

The registry describes NCT03865953 as a completed Phase IIa randomized, placebo-controlled, quadruple-masked crossover study sponsored by Lateral Pharma Pty Ltd. The recorded study dates are 2019-04-09 for the start and 2020-04-19 for primary completion. Enrollment was 53. The conditions listed are neuropathic pain, diabetic peripheral neuropathy and post-herpetic neuralgia.

Participants received oral LAT8881 and placebo in the crossover study. Each treatment description specifies one 30 mg capsule taken twice daily, morning and evening, during the four-week treatment period. The registry’s brief summary characterizes the study as an investigation of efficacy and safety. Crossover studies compare treatment experiences within a study participant, but interpretation can depend on treatment order, period effects and whether an effect persists into a later period. The sequence, washout arrangements and details addressing these issues are not reported in the registry record.

The primary efficacy endpoint was absolute change in mean NPRS score from baseline to Week 4. All efficacy analyses used the per-protocol population; the record says this excluded subjects with inadequate exposure or other major protocol deviations. The posted treatment summaries list 50 observations for LAT8881 and 50 for placebo. These are treatment-specific analysis counts in a crossover record and should not be added to infer the number of participants.

The registry lists 15 outcome measures and 14 secondary outcomes. Secondary measures include pain response thresholds, pain scores at other treatment weeks, maximum change in mean NPRS, functioning and pain-symptom questionnaires. Details of the randomization sequence, the original sample-size rationale and the trial’s 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.

First Intervention (4 Weeks)

Reasons for not completing this period:

Washout/Baseline Period (3 Weeks)

Second Intervention (4 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The per protocol population was used for all efficacy analyses. This population excluded subjects with inadequate exposure to treatment or who had other major protocol deviations.

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 Absolute Change in Mean Pain Score, Using an 11 Point Numeric Pain Rating Scale (NPRS), measured over Baseline to Week 4.

The primary endpoint is change in mean pain intensity from baseline to Week 4, assessed with the 11-point Numeric Pain Rating Scale. The scale ranges from 0, “no pain,” to 10, “worst pain imaginable.” A more negative change indicates a larger reduction in the recorded pain score. The registry describes the outcome as an absolute change and reports a mean and standard deviation for each treatment.

A pain rating provides a standardized way to quantify a participant’s reported pain at specified assessments. Comparing changes, rather than only endpoint scores, places the result in relation to the recorded baseline. The mean summarizes the group’s average change, while the standard deviation describes variation in individual scores around that mean. These summaries help describe the observed response pattern, but they do not show how many participants experienced a particular degree of improvement.

The primary comparison is the net difference between the mean changes on LAT8881 and placebo. Because more negative changes indicate greater reductions, a negative difference favors LAT8881 on the scale’s direction. The registry’s mixed-model estimate was -0.14, with a 95% confidence interval from -0.76 to 0.49. That interval covers both a more negative difference and a difference in the opposite direction, as well as no difference. It therefore communicates uncertainty that is important alongside the point estimate.

The primary endpoint addresses average pain-score change over the stated timeframe. It does not by itself capture every aspect of pain, daily functioning, response for an individual participant or safety.

7. Results Posted in the Registry

• LAT8881: mean -0.87 versus -0.74 on control; difference -0.13 (95% CI -0.85 to 0.59), standardized effect d = -0.07; z-test p = 0.723.

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.

30% Responder Rate in Oral LAT8881 Compared With Placebo, as Assessed by the Numeric Pain Rating Scale.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • LAT8881: 40.0% (20/50) versus 38.0% (19/50) on control; risk difference 2.0 percentage points (95% CI -17.1 to 21.1), risk ratio 1.05 (0.64–1.72); unadjusted two-proportion z-test p = 0.838.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LAT8881 and the control. The interval gives the range of effects that remain compatible with the data.

50% Responder Rate in Oral LAT8881 Compared With Placebo, as Assessed by the Numeric Pain Rating Scale.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • LAT8881: 12.0% (6/50) versus 18.0% (9/50) on control; risk difference -6.0 percentage points (95% CI -19.9 to 7.9), risk ratio 0.67 (0.26–1.73); unadjusted two-proportion z-test p = 0.401.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LAT8881 and the control. The interval gives the range of effects that remain compatible with the data.

Maximum Change in Mean NPRS

• 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:
  • LAT8881: mean -1.53 versus -1.55 on control; difference 0.02 (95% CI -0.52 to 0.56), standardized effect d = 0.01; z-test p = 0.943.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LAT8881 and the control. The interval gives the range of effects that remain compatible with the data.

The reported secondary comparisons cover responder thresholds and maximum change in mean NPRS. Taken together, their directions are not consistent: the two responder thresholds point in opposite directions, and the maximum-change treatment means are close. The comparisons are also uncertain, with the posted recalculated intervals including no difference. This broad pattern does not provide a clear, independent counterpoint to the primary result.

Other listed secondary outcomes concern pain at different weeks and after doses, functioning, pain characteristics and neuropathic symptoms. Their detailed results are not reported in the registry record available for these comparisons, so they cannot be used to strengthen or weaken the primary conclusion. Nor should an absence of detailed results in the registry record be interpreted as a null finding.

Secondary outcomes are often useful for describing the breadth of response and generating hypotheses. They carry less confirmatory weight when many outcomes are examined, because repeated testing increases the chance of at least one apparently notable result by chance. The registry record does not report a multiplicity adjustment or a prespecified testing hierarchy. The unadjusted secondary comparisons are therefore best treated as exploratory, with the primary endpoint remaining the main basis for interpreting efficacy.

Differences in outcome definition and timeframe also matter. A responder threshold asks how many participants cross a specified change boundary, whereas a mean change summarizes the average score shift. Neither measure alone captures all symptom or functional dimensions. The secondary results should be understood as complementary descriptions rather than as interchangeable tests of the same question.

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

• Change in NPRS Score After the First and Last Dose of LAT8881 and Placebo
• Change in Mean Pain Scores After 1, 2 and 3 Weeks of Treatment, Using NPRS
• 30% Responder Rate in Oral LAT8881 Compared With Placebo, as Assessed by the Numeric Pain Rating Scale.
• 50% Responder Rate in Oral LAT8881 Compared With Placebo, as Assessed by the Numeric Pain Rating Scale.
• Maximum Change in Mean NPRS
• Change in Functioning as Assessed by the Brief Pain Inventory Interference Scale (BPI)
• Change in Pain Characteristics and Intensity, as Assessed by the Short Form McGill Pain Questionnaire (SF-MPQ-2)
• Change in Neuropathic Pain Symptoms, as Assessed by Neuropathic Pain Symptom Inventory (NPSI)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference represent?

The mean difference compares the average change under LAT8881 with the average change under placebo. For this comparison, the posted means are -0.87 and -0.74, respectively, and the unadjusted recalculation is -0.13. The sign depends on the subtraction order: the comparison is LAT8881 minus placebo. Since more negative changes represent greater pain-score reductions, a negative difference points toward a larger average reduction under LAT8881. The size of the estimate remains close to zero relative to the uncertainty reported around it.

A mean is useful for summarizing a group, but it can conceal varied individual experiences. The standard deviations, 1.53 for LAT8881 and 2.09 for placebo, describe variability in the treatment-specific change scores. They are not confidence intervals and do not indicate the precision of the estimated treatment contrast by themselves.

Why report a confidence interval?

A confidence interval describes the range of treatment differences compatible with the observed data and the analysis assumptions at the stated confidence level. The registry’s mixed-model estimate is -0.14, with a 95% confidence interval from -0.76 to 0.49. Because the interval includes zero, the data are compatible with no average difference as well as with differences in either direction. A confidence interval is not a guarantee that the true effect lies in that particular interval, and its width matters: a wide interval leaves more possible effect sizes unresolved.

What does the p-value say?

The sponsor’s mixed-model result reports p = 0.67. The simple unadjusted recalculation reports p = 0.723. A p-value describes how unusual data at least as inconsistent with the no-difference hypothesis would be under a specified statistical model, if that hypothesis and model assumptions held. It is not the probability that the no-difference hypothesis is true. The values do not establish equivalence, and a nonsignificant result does not show that an effect is absent.

In general, p-values are sensitive to the analysis model and the assumptions behind it. In a crossover study, treatment observations may be related within participants. A model that accounts for the design can therefore differ from a simple comparison of treatment summaries. The registry identifies the sponsor’s method as mixed models analysis, but model specifications and diagnostics are not reported in the registry record.

Why can over-dispersion matter?

For a binary outcome, such as whether a participant meets a responder threshold, a basic model may assume that outcomes vary according to a specified probability model. Over-dispersion means observed variability is greater than that model expects. If present and ignored, uncertainty can be understated, making confidence intervals too narrow and statistical evidence appear stronger than it is. This is a general statistical consideration, not a reported finding about this trial. The registry record does not report an over-dispersion assessment for the secondary responder outcomes.

The responder outcomes are counts under each treatment, and the accompanying unadjusted recalculations compare the proportions represented by those counts. Those calculations do not replace the trial’s crossover analysis. The registry does not report sponsor analyses for these secondary outcomes in the listed results, so details of any design-aware binary models are not available in the registry record.

How should secondary outcomes be treated?

Secondary outcomes can describe other dimensions of pain and functioning and can help identify questions for later studies. However, testing many outcomes creates more opportunities for chance findings. A multiplicity strategy may control the overall chance of false-positive conclusions, for example by adjusting significance thresholds or specifying a hierarchy of tests. Whether the trial used such a strategy is not reported in the registry record. The posted unadjusted secondary comparisons should consequently be regarded as exploratory rather than as independent confirmatory evidence.

General statistical interpretation also depends on the analysis population, missing-data handling and adherence to the planned model. The efficacy population was per protocol, excluding participants with inadequate exposure or major protocol deviations. The registry does not report the number or reasons for exclusions, the missing-data method, or whether sensitivity analyses assessed the effect of those choices. These omissions limit assessment of the assumptions behind the estimates.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the estimated treatment difference. The registry’s primary mixed-model estimate is -0.14, and its 95% confidence interval extends from -0.76 to 0.49. This range includes zero and includes estimates on either side of zero. It therefore leaves uncertainty about the direction and size of the average treatment difference, even though the point estimate itself is close to zero.

The simple unadjusted recalculation also has an interval that crosses zero. Its point estimate is -0.13 and its p-value is 0.723. The precise recalculated interval endpoints are not needed to interpret the key feature: it does not isolate an effect in one direction. The sponsor’s reported model-based interval is the primary inferential result in the registry.

Intervals should be read in the units of the outcome: NPRS score change. They do not describe the range of individual participants’ changes; they describe uncertainty in the estimated treatment contrast. The standard deviations of 1.53 and 2.09 describe spread in the treatment-specific scores, a different quantity from uncertainty around the mean difference.

Precision is shaped by variability, analysis design and the amount of information contributing to the estimate. The efficacy summaries list 50 observations under each treatment, while the overall enrollment is 53. Because this is a crossover trial, the treatment-specific counts should not be interpreted as independent participant groups or added together. The registry does not report enough participant-flow detail to explain the relationship between enrollment and the per-protocol analysis counts.

A confidence interval spanning zero is not proof of no effect; rather, it indicates that the posted analysis does not estimate the effect with enough precision to exclude no difference at the stated confidence level. It also does not establish that any possible effect would be clinically important. The registry record does not report a threshold defining a clinically important NPRS difference for this study.

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. The event-count convention is relevant only to time-to-event outcomes; the outcomes described for this trial are continuous or binary. The planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers detecting the stated fraction of the observed effect: 100%, 75% or 50%.

The 80% power column gives the planned number of participants per arm under which the assumed effect would be detected at the stated significance level in 80% of repeated studies, if the planning assumptions and effect size held. The 90% power column describes the corresponding planning target for 90% of repeated studies. These percentages describe design targets, not the probability that the trial result is correct.

As the assumed effect becomes smaller, more participants are needed to distinguish it from random variation at the same power and significance level. The figures are illustrations calculated from the observed effect, not the original design basis. The trial’s original sample-size assumptions are not reported in the registry record. This is not observed power: it is a planning exercise, and it does not establish what the completed study was capable of detecting under its actual design and analysis.

For a crossover trial, the displayed per-arm wording should be read as a planning convention for the calculation, not as a statement that the study had independent parallel groups. The registry does not report a crossover-specific sample-size calculation, nor does the illustration account for unreported design details such as within-participant correlation or treatment-period effects. The planning numbers therefore do not reconstruct the sponsor’s original sample-size justification.

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 = 1.832.
2. n = 2 × (1.96 + 0.842)² × 1.832² / -0.130² = 3,115.9, rounded up to 3,116 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 <- 1.8315294155432                     # 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(3865953)
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 = 3,116 (80% power), 4,172 (90% power)
 75% of observed effect: n per arm = 5,540 (80% power), 7,416 (90% power)
 50% of observed effect: n per arm = 12,464 (80% power), 16,686 (90% power)
power.t.test: 3116.8 
Simulated power at n = 3,116 per arm: 0.800 (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 registry reports the sponsor’s primary analysis as a mixed models analysis. Its net mean difference is -0.14, with a 95% confidence interval from -0.76 to 0.49 and p = 0.67. The separate recalculation from the posted treatment summaries is an unadjusted comparison: it gives a mean difference of -0.13 and p = 0.723. Both estimates are close to zero and both intervals include no difference.

The recalculation is useful as a transparent check on the direction and approximate scale of the posted summaries. It does not reproduce the sponsor’s model or account for unreported modeling details of the crossover design. The estimates need not match exactly because the calculations use different statistical approaches. The registry does not flag a discrepancy between the results.

Interpretation should therefore start with the sponsor’s reported mixed-model result, which is the trial’s own stated analysis. The recalculation supports the broad reading that the estimated average difference is small relative to the uncertainty, but it is not a replacement for the mixed-model analysis. The registry record does not provide the full model specification, assumptions or diagnostics needed for an independent assessment of that analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 15 outcome measures, including the primary pain-score change and secondary outcomes addressing pain response, pain over time, functioning and symptom characteristics. When many outcomes are tested, the chance of obtaining one apparently favorable result by chance can increase. A multiplicity plan can address this through methods such as adjusting thresholds or controlling the order in which outcomes are tested. Whether the trial prespecified such a plan, and whether any adjustment was used, are not reported in the registry record.

The posted secondary recalculations are unadjusted. Their p-values should not be treated as confirmatory evidence independent of the primary analysis. The absence of a reported multiplicity procedure does not prove that no procedure was used; it means the registry record does not document one. The full statistical analysis plan and any prespecified hierarchy are not reported in the registry record.

All efficacy analyses used the per-protocol population, which excluded subjects with inadequate exposure or other major protocol deviations. This defines the population represented by the posted efficacy summaries, but the record does not report the number of exclusions, their reasons, or a comparison with an intention-to-treat analysis. How participants were handled when observations were missing, including any imputation or sensitivity analysis, is not reported in the registry record.

These details matter because exclusions and missing outcomes can affect the estimate if the analyzed observations differ systematically from those not analyzed. In crossover studies, treatment order and period can also influence how observations are interpreted. The registry identifies mixed models analysis for the primary outcome, but the model terms, missing-data assumptions and diagnostics are not reported in the registry record. The available information supports reading the reported estimate and its uncertainty, but does not allow a complete audit of the analysis strategy.

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 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events for LAT8881 and zero for placebo. It also reports zero deaths for both treatment conditions. These are the serious-event summaries in the record; no serious adverse-event terms are listed.

The registry lists 51 participants at risk for serious adverse events under each treatment condition. These treatment-specific figures should be read as reported and not added together to infer a number of unique participants in this crossover study. A zero count in the posted summary means no serious event was recorded in that category for the stated analysis; it does not establish that serious events are impossible or that the treatment has no safety risks.

The record also lists other adverse events affecting 5 participants under LAT8881 and 6 under placebo. These are not serious adverse events and should not be conflated with the serious-event counts. The registry summary does not provide further context about event types, timing, severity or attribution in the information. Safety interpretation is therefore limited to the posted counts and should be considered separately from the efficacy estimate.

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

The primary result describes the average change in NPRS pain score from baseline to Week 4 in the per-protocol efficacy analysis. The sponsor’s mixed-model estimate was -0.14, with a 95% confidence interval from -0.76 to 0.49 and p = 0.67. The point estimate is close to zero, and the interval includes no difference. The data therefore do not establish a clear average difference between LAT8881 and placebo in this analysis.

This result does not prove that the treatments have identical effects. The confidence interval allows for possible differences in either direction, and the registry does not report a clinically important difference threshold for interpreting the NPRS scale in this trial. A lack of clear statistical separation should not be translated into a claim of equivalence or into a claim that no participant experienced a change.

The result is limited to the defined outcome, timeframe and analysis population. It concerns mean score change, not individual response, all dimensions of neuropathic pain, longer-term outcomes or every listed secondary measure. The efficacy analyses used a per-protocol population that excluded subjects with inadequate treatment exposure or major protocol deviations. Results may not directly represent every enrolled participant.

The study also reports safety counts, including no serious adverse events and no deaths in the posted treatment-specific summaries. Those counts are descriptive and do not establish the absence of risk. The record does not provide the detail needed to characterize all event types or their relationship to treatment.

Overall, the posted evidence is an estimate with meaningful uncertainty rather than a definitive statement about efficacy or safety. It should be interpreted as a result from this completed Phase IIa crossover study, not generalized automatically to other populations, treatment durations or clinical settings.

18. Why This Trial Matters Statistically

This trial illustrates why the point estimate, uncertainty interval and analysis design need to be read together. The primary mean difference is close to zero, but the confidence interval includes values on either side of zero. Looking only at the estimate or only at its p-value would discard important information about the range of effects compatible with the data.

The crossover design also makes the relationship between observations important. Participants contribute treatment experiences under both conditions, so a model accounting for within-participant structure may differ from a simple comparison of treatment summaries. The registry reports a mixed-model primary analysis and permits an unadjusted recalculation from the posted summaries, but it does not report enough model detail to reproduce the sponsor’s analysis fully.

The record further distinguishes a planned sample-size illustration from the study’s original design rationale. Planning figures based on the observed effect can show how required sample size changes with assumed effect size, but they do not reveal the design assumptions used before the trial began and are not observed power. Keeping those interpretations separate prevents retrospective planning calculations from being mistaken for evidence about the trial’s original design.

Finally, the trial shows why secondary outcomes and safety summaries require context. Multiple unadjusted comparisons can generate chance findings, while a zero serious-event count is a descriptive observation rather than proof of no risk. Statistical interpretation depends not only on numerical results but also on the stated population, model, endpoint definitions and limits of registry reporting.

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 record does not report the crossover sequence, washout arrangements, period-specific results or analyses of carryover and period effects. These design details matter because treatment experiences in a crossover study are not necessarily independent. Although the primary method is identified as mixed models analysis, the model specification and its assumptions are not reported in the registry record.

The efficacy analysis used a per-protocol population that excluded subjects with inadequate exposure or other major protocol deviations. The number and reasons for exclusions, participant flow by treatment period, and any intention-to-treat or sensitivity analyses are not reported. The treatment-specific analysis counts therefore cannot be fully reconciled with overall enrollment from the record alone.

Missing-data handling is not reported in the registry record. The record also does not document a multiplicity strategy for the numerous outcomes, nor does it give the original sample-size assumptions or justification. This makes it difficult to assess how the study was planned to handle multiple comparisons and what effect size its original design targeted.

The primary result concerns mean NPRS change at Week 4, and the registry does not report a clinical-importance threshold for that scale in this study. Detailed results for the full set of listed secondary outcomes are not reported in the registry record used for these comparisons. Safety reporting is also limited to the posted adverse-event counts, without detailed event descriptions or attribution information.

These limitations do not invalidate the posted estimates, but they constrain how fully their assumptions and generalizability can be assessed. Interpretation should remain tied to the analyzed population, stated timeframe and available outcome detail.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Oral LAT8881 in Neuropathic Pain — NCT03865953.
• Registry record last updated 2021-06-14; status last verified 2021-04.
• Results first posted 2021-04-23.
• 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

NCT03865953 is a completed, randomized, quadruple-masked, placebo-controlled crossover Phase IIa study of oral LAT8881 in neuropathic pain. The registry lists diabetic peripheral neuropathy and post-herpetic neuralgia among the conditions. Enrollment was 53. LAT8881 and placebo were each described as one 30 mg capsule taken twice daily during the four-week treatment period.

The primary endpoint was mean NPRS change from baseline to Week 4. The registry’s mixed-model estimate was -0.14, with a 95% confidence interval from -0.76 to 0.49 and p = 0.67. This interval includes no difference. Efficacy analyses used the per-protocol population.

The record lists zero serious adverse events and zero deaths under each treatment condition. Details of crossover sequencing, missing-data handling, multiplicity procedures and the original sample-size rationale are not reported in the registry record.