Safety/Efficacy Study of Retigabine vs. Placebo in Post-Herpetic Neuralgia (PHN): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety/Efficacy Study of Retigabine vs. Placebo in Post-Herpetic Neuralgia (PHN) (NCT00612105), a randomized phase 2 study. The primary outcome is Primary Endpoint Will be the Change From Baseline in Average Pain Score Over the Last 7 Days of the Maintenance Phase..

2. Clinical Question

Pain was recorded each evening in an electronic diary. Participants rated pain experienced during the previous 24 hours using an 11-point Numerical Rating Scale, from 0 for no pain to 10 for severe pain. The primary outcome compared the baseline average with the average for the last 7 days of the Maintenance Phase. A more negative change represents a larger reduction in the recorded score from baseline.

The trial was a phase 2a proof-of-concept study. Its stated purpose was to evaluate retigabine versus placebo for pain associated with post-herpetic neuralgia. The registry record does not report a formal hypothesis statement beyond that purpose, or a threshold defining a clinically important difference. The question is therefore best read as a comparison of the recorded group changes and their uncertainty, rather than as a definitive test of clinical benefit.

3. Trial Design

This was a randomized, quadruple-masked, parallel-group phase 2a study comparing retigabine with placebo. The registry lists the trial as completed and gives enrollment as 187. The study started in 2007-10, with primary completion in 2009-05. The sponsor was Bausch Health Americas, Inc.

The primary outcome was assessed at baseline and Week 4 of the Maintenance Phase. The registry describes a titration period before maintenance and defines the primary analysis population using completion, treatment exposure, diary completion, and protocol-adherence criteria. The primary analysis was therefore not described as including every randomized participant: it was restricted to participants meeting the Per Protocol criteria.

Randomization and masking are important design features for a treatment comparison. Random assignment is intended to reduce systematic differences between groups at entry, while masking is intended to limit the influence of treatment knowledge on care, reporting, and assessment. These features do not remove uncertainty due to sample size, missing observations, or the chosen analysis population. The record identifies quadruple masking but does not specify in the registry record which roles were masked.

The registry lists retigabine and placebo as the interventions and reports a range of additional outcomes, including pain assessments, rescue medication use, responder classifications, sleep measures, and patient global impression. The record lists 23 outcome measures and one reported analysis. The protocol’s original sample-size justification, planned interim analyses, and detailed 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.

Period Title 1: 6-Week Titration Phase

Reasons for not completing this period:

Period Title 2: 4-Week Maintenance Phase

Reasons for not completing this period:

Period Title 3: 3-Week Taper Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per Protocol (PP) Population: all randomized participants who completed the Titration Phase, had at least 1 dose of treatment in the MP, had at least 3 diary entries in the MP, and did not have any protocol violations or any 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 Primary Endpoint Will be the Change From Baseline in Average Pain Score Over the Last 7 Days of the Maintenance Phase., measured over Baseline and Week 4 (Maintenance Phase-MP).

The primary endpoint is change from baseline in average pain score over the last 7 days of the Maintenance Phase. The change was defined as the average diary pain score for those final days minus the baseline average. Baseline was based on the post-washout period and included the average of the last 7 available entries before or including the diary measurement on Titration Day 0.

Participants recorded pain every evening, rating pain experienced during the previous 24 hours on an 11-point Numerical Rating Scale. The scale runs from 0, no pain, to 10, severe pain. Averaging diary entries over a period is intended to represent pain across multiple days rather than relying on a single assessment. Comparing the end-of-maintenance average with baseline expresses the outcome as change over time, and comparing that change between randomized groups helps distinguish the observed group patterns from changes also seen with placebo.

The endpoint is reported as a least-squares mean with a standard error for each group, and the sponsor reports an adjusted mean difference. The primary analysis population was per protocol, with eligibility criteria based on completing titration, treatment exposure, diary entries, and protocol adherence. That population definition matters: the result describes participants meeting those criteria, and does not automatically describe every randomized participant.

The endpoint measures a reported pain score. It does not, by itself, establish why scores changed or whether a difference would be important to participants. The registry record does not report a threshold for clinical importance.

7. Results Posted in the Registry

• 1: Retigabine: mean -2.65 versus -2.22 on control; difference -0.43 (95% CI -1.46 to 0.60), standardized effect d = -0.14; z-test p = 0.412.

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 to the End of the MP (Included All Participants Who Completed Week 4 of the MP and Who Terminated Early During the MP) in Sleep Quantity

• 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:
  • 1: Retigabine: mean 0.50 versus 0.20 on control; difference 0.30 (95% CI -0.16 to 0.76), standardized effect d = 0.20; z-test p = 0.204.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 1: Retigabine and the control. The interval gives the range of effects that remain compatible with the data.

Scores for Reported Health Transition at the End of the MP for All Participants Who Completed Week 4 of the MP and Who Terminated Early During the MP

• 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:
  • 1: Retigabine: mean 2.68 versus 2.37 on control; difference 0.31 (95% CI -0.01 to 0.63), standardized effect d = 0.33; z-test p = 0.055.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 1: Retigabine and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in the Average Diary Pain Score to the Last 7 Days of the Maintenance Phase by Post Herpetic Neuralgia (PHN) Subtype "Irritable Nociceptors"

• 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:
  • 1: Retigabine: mean -1.78 versus -2.85 on control; difference 1.07 (95% CI -0.49 to 2.63), standardized effect d = 0.49; z-test p = 0.180.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 1: Retigabine and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary outcomes addressing pain over time, rescue medication, responder status, sleep, and patient-reported impressions. The posted secondary results include continuous outcomes and a pain subtype analysis. These measures can add context about different aspects of the study, but they do not all measure the same construct as the primary diary-based pain change.

The available secondary estimates do not provide a uniform, highly precise pattern that could resolve the uncertainty in the primary comparison. Their confidence intervals are broad enough to include no difference, and the secondary analyses are not reported as adjusted ANCOVA comparisons. They should therefore be read as exploratory or supportive information rather than as independent confirmation of a treatment effect. No individual secondary estimate should be elevated above the prespecified primary endpoint simply because its point estimate appears more favorable.

Multiplicity matters because the more outcomes and comparisons examined, the greater the chance that at least one result will look unusual by chance. The registry lists 23 outcome measures and 22 posted secondary outcomes, but a multiplicity procedure is not reported in the registry record. Without knowing whether outcomes were prespecified as confirmatory or whether adjustment was used, unadjusted secondary p-values carry less weight than a single prespecified primary comparison.

The secondary outcomes may help generate questions for further study, including whether pain patterns vary across measures or whether patient-reported sleep and health transition align with pain ratings. They cannot establish such patterns conclusively from this record alone. The primary endpoint remains the central result, and its uncertainty is not removed by considering multiple secondary outcomes.

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

• Change From Baseline to Weeks 2 and 4 of the Maintenance Phase in Mean In-clinic Pain Assessment
• Number of Rescue Medication Tablets Taken Per Day During the Maintenance Phase (MP)
• Change From Baseline in Pain Intensity Score at Each Week During the Maintenance Phase (MP)
• Number of Participants Classified as Responders, With a 50% and 30% Pain Reduction From Baseline to the Last 7 Days of the Maintenance Phase
• Change From Baseline to the End of the MP (Included All Participants Who Completed Week 4 of the MP and Who Terminated Early During the MP) in Medical Outcomes Study (MOS) Sleep Scale Scores
• Change From Baseline to the End of the MP (Included All Participants Who Completed Week 4 of the MP and Who Terminated Early During the MP) in Sleep Quantity
• Number of Participants With the Indicated Change From Baseline to the End of the Maintenance Phase in Optimal Sleep Based on the Sleep Quantity Domain of the MOS Sleep Scale
• Number of Participants With the Indicated Overall Patient Global Impression of Change (PGIC)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numeric pain score summarized as change from baseline. For a continuous outcome, a group mean describes the central value of the observations, while a mean difference expresses the contrast between two group means. Here, a negative change means the score at the end of maintenance was lower than the baseline score. A negative between-group difference means the retigabine group’s estimated change was more negative than the placebo group’s, based on the stated direction of subtraction.

What does ANCOVA contribute?

The sponsor reports an ANCOVA analysis. In general, analysis of covariance compares groups while accounting for a covariate or covariates specified in the analysis. In clinical trials, adjustment can account for baseline values or other prespecified factors and may improve precision when those factors are related to the outcome. The registry record names ANCOVA but does not report the full model specification, the covariates used, or the detailed assumptions. Those details should not be inferred from the method label alone.

The sponsor’s adjusted mean difference is -0.43. The posted group summaries also allow a simple unadjusted comparison, which has the same point estimate but a different confidence interval and p-value. That recalculation does not reproduce ANCOVA: the group-level summaries do not contain the participant-level information needed to fit the sponsor’s model. Since the discrepancy flag is false, there is no stated conflict requiring a different reading; the sponsor’s reported analysis remains the primary inferential result.

What do the standard errors describe?

The primary group estimates are least-squares means, and the registry gives a standard error for each. A standard error describes the estimated sampling uncertainty of an estimate: across repeated studies conducted under comparable conditions, estimates would vary. It is not the spread of individual participants’ pain scores. Standard deviations, when reported for other outcomes, instead describe variation among individual observations. Confusing standard errors with standard deviations can make an estimate appear more or less variable than it is.

The sponsor’s estimate is accompanied by a 95% confidence interval. In general, a confidence interval gives a range of values compatible with the estimate under the analysis and its assumptions. Wider intervals indicate less precision; narrower intervals indicate greater precision. The interval is not a guarantee that the true effect lies within its endpoints, nor does it show the probability that a particular effect is true. Its interpretation depends on the sampling and model assumptions used.

Why can analyses yield different intervals?

The unadjusted recalculation is based on the posted group means, standard errors, and group sizes, with an estimated pooled standard deviation described as approximate. The sponsor’s ANCOVA uses an adjusted model. Adjustment, variance estimation, and the information included in the analysis can change the standard error and interval even when the estimated mean difference is the same. This is why the recalculated interval should be treated as a transparent, simple check rather than a replacement for the reported model.

The primary endpoint uses a diary average over the last 7 days, rather than one pain rating. In general, averaging repeated measurements can reduce the influence of an unusually high or low observation, although it does not eliminate measurement error or missing-data concerns. The registry specifies the relevant averaging windows and the Per Protocol eligibility criteria, but missing-data procedures are not reported in the registry record.

Why does over-dispersion matter?

Over-dispersion is a general concern for some outcome models, especially models for counts, when observations vary more than the model’s assumed distribution allows. If that extra variability is ignored, uncertainty can be understated and inferential results can be too optimistic. The primary endpoint is a continuous pain-score change, and the registry names ANCOVA for the sponsor analysis. Over-dispersion is not reported as an issue for this analysis; it should not be assumed to have been assessed or to have affected the result. It can nevertheless matter when evaluating other trial outcomes, such as counts of rescue medication use, if those outcomes are modeled as counts.

The registry also describes responder outcomes based on specified reductions in pain, as well as sleep and patient-reported measures. Different outcome types call for different statistical summaries and models. A continuous mean change does not answer the same question as the proportion classified as a responder, and a result on one outcome should not be substituted for another. The registry record does not provide a complete statistical plan describing model choices across all outcomes.

Finally, p-values and confidence intervals answer related but distinct questions. A p-value measures how incompatible the observed data are with a specified null model under the analysis assumptions; it is not the probability that the null hypothesis is true. A confidence interval displays a range of effect estimates compatible with the data and model at its stated confidence level. Neither statistic conveys clinical importance by itself. Interpreting the result requires attention to the effect’s direction, its uncertainty, the analysis population, and the outcome’s meaning.

11. Confidence Intervals and Precision

The sponsor’s 95% confidence interval for the adjusted primary mean difference runs from -1.171 to 0.312. It includes no difference and extends to estimates in both directions. Thus the point estimate alone does not convey the full uncertainty: the observed estimate is -0.43, but the data and model are compatible with a range of effects that includes a small difference favoring either group.

The unadjusted recalculation gives a confidence interval from -1.458 to 0.598. It is wider than the sponsor’s interval and also includes no difference. The distinction reflects the different analysis methods, not a contradiction in the point estimate. Because the sponsor reports ANCOVA as the trial analysis, that adjusted result is the appropriate primary reference; the unadjusted result is a separate summary-based calculation.

Confidence intervals describe statistical precision, not clinical importance. The registry does not report a threshold for a clinically important change in pain score, so the interval cannot be classified against such a threshold from the record. Nor does the interval establish that all values it spans are equally plausible in a practical sense. It indicates the uncertainty remaining under the analysis and assumptions.

The interval’s inclusion of no difference means the posted result does not sharply distinguish the groups. It should not be interpreted as proof that the groups are identical. Conversely, the negative point estimate should not be treated as proof of a favorable treatment effect. The uncertainty is material to both claims. The per-protocol population and unreported missing-data details further limit what can be concluded about precision for the full randomized population.

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 illustrations use the observed primary effect as their starting point and show planning scenarios for detecting the full observed effect, 75% of it, or 50% of it. For each scenario, the figures are participants per arm for 80% power and participants per arm for 90% power. They are not total events. For the full observed effect, the illustration gives 780 participants per arm for 80% power and 1,044 participants per arm for 90% power. For 75% of the observed effect, it gives 1,387 participants per arm for 80% power and 1,856 participants per arm for 90% power. For 50% of the observed effect, it gives 3,119 participants per arm for 80% power and 4,176 participants per arm for 90% power.

The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. In plain terms, the 80% column describes the planned sample size under which the calculation assigns an 80% chance of detecting an effect of that size if it is present and the assumptions hold; the 90% column uses a higher target chance. Higher power generally requires more participants. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants as the target effect becomes smaller.

These are planning illustrations based on the observed estimate, not the trial’s original design calculations. The original sample-size justification and assumptions are not reported in the registry record. This is not observed power: the figures do not measure how much power the completed trial actually had, and they should not be used to reinterpret the trial’s result as if a post-study power calculation could resolve its uncertainty.

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 = -0.430; pooled standard deviation σ = 3.031.
2. n = 2 × (1.96 + 0.842)² × 3.031² / -0.430² = 779.7, rounded up to 780 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 <- -0.43                      # observed difference in means
sigma <- 3.03056053459523                     # 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(612105)
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 = 780 (80% power), 1,044 (90% power)
 75% of observed effect: n per arm = 1,387 (80% power), 1,856 (90% power)
 50% of observed effect: n per arm = 3,119 (80% power), 4,176 (90% power)
power.t.test: 780.7 
Simulated power at n = 780 per arm: 0.801 (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 reports an ANCOVA estimate of -0.43 for the primary mean difference, with a 95% confidence interval from -1.171 to 0.312 and p = 0.254. A simple recalculation from the posted group summaries gives the same point estimate, -0.43, but a confidence interval from -1.458 to 0.598 and p = 0.412. The sponsor’s analysis takes precedence because it is the trial’s reported adjusted analysis; the recalculation is an unadjusted comparison and does not reproduce the ANCOVA model.

The estimates therefore agree on the direction and point estimate, but differ in their uncertainty and p-value. That difference is consistent with using different methods and information. Both intervals include no difference, so neither analysis provides a precise separation between the groups. The registry indicates no discrepancy between the reported analysis and recalculation. The sponsor’s result should be used for the trial’s primary inferential conclusion, while the recalculation can help readers see how an unadjusted summary comparison behaves.

The registry names ANCOVA but does not report all model details, such as the covariates or full variance specification. That limits independent reconstruction of the sponsor’s analysis from the registry record. The recalculation is not a correction to the sponsor result and should not be presented as if it were an alternative prespecified analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 23 outcome measures, including the primary pain endpoint and a range of secondary measures. It reports one analysis. The record does not report a multiplicity adjustment, a hierarchy of confirmatory secondary hypotheses, or a complete statistical analysis plan. Consequently, it is not possible to determine from the registry record whether the secondary tests were intended to support formal claims or to describe additional outcomes.

Multiplicity is the general problem of interpreting multiple statistical tests. As more outcomes or comparisons are examined, there are more opportunities for a nominally unusual result to arise by chance. Adjustments or prespecified testing sequences can help control that risk, but their use and details are not reported in the registry record. This makes isolated secondary p-values less persuasive than the primary analysis, especially when many outcomes are listed.

Missing-data handling is also not reported in the registry record. The primary endpoint required diary observations, and the Per Protocol population required at least 3 Maintenance Phase diary entries as well as completion and adherence criteria. The registry does not describe how missing diary entries were handled in calculating the endpoint, whether values were imputed, or how participants excluded from the Per Protocol analysis were treated in other analyses. These details matter because missingness and exclusions can affect both the estimated effect and its precision.

The registry does not report whether interim analyses were planned or conducted, nor does it give the original sample-size justification. Those aspects should remain unknown rather than inferred from the completed study’s outcome summaries. The posted record supports interpretation of the stated analysis and population, but not a reconstruction of every decision in the trial’s statistical plan.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: asthma (1.6%), chronic obstructive pulmonary disease (1.6%), atrial fibrillation (1.6%), pneumonia (1.6%), maculopathy (0.8%).

The registry reports serious adverse events affecting 7 among 125 participants in the retigabine group and 1 among 62 in the placebo group. Other adverse events affected 98 among 125 in the retigabine group and 29 among 62 in the placebo group. These are the posted counts and denominators; they describe reported events in the registry and do not by themselves establish that treatment caused an event. The registry record does not report death counts.

The serious adverse event terms listed include asthma, chronic obstructive pulmonary disease, atrial fibrillation, and pneumonia, each reported as 1.6%, as well as maculopathy and retinal detatchment, each reported as 0.8%. These term-level percentages should be read as registry-reported safety descriptions, not as a complete assessment of comparative risk. The record does not report enough detail to determine event timing, severity beyond the serious classification, relatedness assessments, or the full clinical context.

Safety counts require caution because the denominators differ from the enrollment and primary-analysis populations. The registry does not explain the relationship between these safety denominators and the participants included in each efficacy analysis. The figures can describe what was recorded, but they do not establish a causal comparison or prove that unlisted events did not occur.

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

The primary result is an estimated between-group difference in change in diary pain score over the last 7 days of the Maintenance Phase. The point estimate is -0.43, with a sponsor-reported 95% confidence interval from -1.171 to 0.312. It is numerically in the direction of a larger reduction for retigabine, but the interval includes no difference and extends to estimates in the opposite direction. The result is uncertain rather than a precise demonstration of separation between groups.

This does not establish that the groups were identical. A result with an interval including no difference can arise when the true difference is absent or when the data are not precise enough to distinguish a difference from no difference. Nor does the point estimate establish a clinically important effect. The registry record does not report a threshold for clinical importance, and a statistical estimate alone does not establish how meaningful a score change would be to participants.

The primary analysis applies to the Per Protocol population, defined using completion, treatment exposure, diary completion, and protocol-adherence criteria. It should not automatically be generalized to every randomized participant. Missing-data procedures and the primary analysis of all randomized participants are not reported in the registry record, so the robustness of the estimate to those choices cannot be evaluated from this record.

The trial was a phase 2a proof-of-concept study. Its results describe the observed outcome in this study and the uncertainty around the reported comparison; they do not establish a general treatment recommendation or answer every question about efficacy and safety. Secondary outcomes can offer context, but the multiplicity and reporting limitations mean they should not be used to override the primary result.

In general, statistical evidence, clinical importance, and causal interpretation are related but distinct. Randomization and masking strengthen the comparative design, while uncertainty, analysis population, outcome measurement, and unreported analytic details still matter. The registry supports a cautious description of the observed scores, not a claim that retigabine does or does not work.

18. Why This Trial Matters Statistically

This trial illustrates why an estimated effect should be read together with its uncertainty. The primary point estimate is straightforward to state, but the sponsor’s confidence interval includes no difference and spans values in both directions. Looking only at the point estimate could overstate what the data establish; looking only at whether a p-value crosses a threshold would also discard information about the range and direction of compatible effects.

It also demonstrates that adjusted and unadjusted analyses can share a point estimate yet give different measures of uncertainty. The sponsor’s ANCOVA result is the relevant reported analysis, while the simple recalculation is useful for understanding the summary data but cannot reproduce the model. Keeping those roles distinct prevents a recalculation from being mistaken for the trial’s own inferential analysis.

The choice of population matters as well. The primary result applies to the Per Protocol population, which had defined completion, diary, treatment, and adherence requirements. Such criteria describe who contributed to the primary analysis, but can also narrow the population to which the estimate directly applies. The registry does not provide missing-data details or an all-randomized primary result to compare.

Finally, the record lists many secondary outcomes alongside a primary endpoint. This makes multiplicity and outcome hierarchy central to interpretation: a collection of supportive measures is not equivalent to one decisive confirmatory result, particularly when adjustment is not reported. Together, these features make the study a useful example of why design, analysis population, endpoint definition, precision, and reporting completeness all belong in a statistical reading of a clinical trial.

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 primary efficacy analysis is restricted to the Per Protocol population. Its criteria require completion of titration, treatment exposure during maintenance, diary entries, and absence of protocol violations or major deviations. The registry does not report a corresponding primary analysis of all randomized participants, so the degree to which the result depends on this population restriction cannot be assessed.

Missing-data methods are not reported in the registry record. This is relevant because the endpoint depends on repeated electronic diary entries and the analysis population has a minimum diary-entry requirement. The record does not explain how incomplete diaries, early termination, or other missing values were handled for the primary endpoint. It also does not report a sensitivity analysis for missing data.

The sponsor identifies ANCOVA but does not report the complete model specification in the registry record. The covariates, model diagnostics, and detailed variance assumptions are therefore unavailable for independent evaluation. The simple unadjusted recalculation cannot fill that gap, since it is based on group summaries and does not reproduce participant-level adjustment.

The registry lists many outcomes, but does not report a multiplicity strategy or clearly distinguish confirmatory from exploratory secondary analyses. It also does not report the trial’s original sample-size justification or interim-analysis plan. These omissions limit assessment of how the analysis was planned and how secondary findings should be weighted.

Finally, the registry does not report a clinical-importance threshold for the pain score, detailed dose levels, or the full context of safety events. The posted results support interpretation of the stated outcomes and estimates, but these missing details restrict broader conclusions about clinical meaning, analytic robustness, and safety.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety/Efficacy Study of Retigabine vs. Placebo in Post-Herpetic Neuralgia (PHN) — NCT00612105.
• Registry record last updated 2018-05-08; status last verified 2018-04.
• Results first posted 2012-01-11.
• 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

NCT00612105 was a randomized, quadruple-masked, parallel-group phase 2a study of retigabine versus placebo for post-herpetic neuralgia. The registry lists enrollment of 187, a start in 2007-10, primary completion in 2009-05, and completed status.

The primary endpoint was change from baseline in average diary pain score over the last 7 days of the Maintenance Phase. The sponsor’s ANCOVA estimate was -0.43, with a 95% confidence interval from -1.171 to 0.312 and p = 0.254. The interval includes no difference, so the estimate remains uncertain. A summary-based unadjusted recalculation gives the same point estimate but a different interval and p-value; the sponsor’s analysis takes precedence.

The primary analysis used a Per Protocol population. The registry lists 23 outcome measures, but multiplicity procedures, detailed missing-data methods, the original sample-size justification, and full model details are not reported in the registry record. Safety counts are descriptive and do not establish causation.