Clinical Management of Neuropathic Pain With Ramelteon: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Management of Neuropathic Pain With Ramelteon (NCT00753623), a randomized na study. The primary outcome is Difference in Visual Analog Scale (VAS) for Pain (0-10) Between Treatments.

2. Clinical Question

The study proposal states the hypothesis that ramelteon would reduce pain scores and improve functional status in people with neuropathic pain. The posted primary outcome concerns pain scores; a functional-status outcome is not reported in the registry record. Thus the statistical question that can be assessed from the posted results is limited to the reported pain measure, not the broader proposed hypothesis.

3. Trial Design

The registry record describes a randomized crossover study comparing ramelteon with placebo in people with neuropathic pain. In a crossover design, participants receive more than one treatment in a planned sequence, so each participant can contribute observations under both treatments. The record lists two sequences: ramelteon first and placebo second, or placebo first and ramelteon second. The reported primary analysis includes 15 participants who completed both phases.

The registry lists masking as triple. The arm descriptions refer to the study as double-blind and say that neither participants nor study staff would know the assigned intervention. The specific roles included in the registry’s triple-masking label are not reported in the registry record, so these descriptions do not establish exactly who else was masked. The record identifies ramelteon and placebo as drug interventions and gives an 8mg once-a-night dose for ramelteon.

The trial status is terminated. The record reports enrollment of 23, a start in 2008-09, and primary completion in 2010-12. The reason for termination is not reported in the registry record. The phase is listed as NA. Details such as the planned duration of treatment phases, washout arrangements, randomization method, allocation concealment, and the original statistical design assumptions are not reported in the registry record.

A crossover comparison can benefit from comparing treatment responses within the same participant, but that requires an analysis suited to the paired structure and sufficient information about sequence and period. The posted summaries do not describe whether the sponsor’s test accounted for within-participant pairing, treatment sequence, or period. Those features of the statistical analysis 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.

Phase I (14 Days)

Reasons for not completing this period:

Washout (7 Days)

Reasons for not completing this period:

Phase II (14 Days)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Only 15 subjects completed both treatment phases so we only included these subjects in the analysis.

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 Difference in Visual Analog Scale (VAS) for Pain (0-10) Between Treatments, measured over VAS score at baseline and after the treatment period.

The primary outcome is the difference in Visual Analog Scale pain scores between treatments, with the score assessed at baseline and after a treatment period. Participants rated pain on a scale from 0, no pain, to 10, the worst pain they could imagine. The outcome is reported as a mean, with standard deviation as the measure of spread. The registry record states that a negative number indicates improvement from baseline.

Pain ratings are used as a direct way to capture a participant’s reported experience of pain. A numeric scale makes it possible to summarize changes across participants and compare average changes between treatment conditions. The mean describes the average reported change, while the standard deviation describes how much participants’ changes varied around that average. Neither summary alone reveals the full distribution of individual responses.

The posted treatment means are changes from baseline: -1.0 for ramelteon and -1.1 for placebo. The reported comparison is a mean difference of 0.1. Because the endpoint description defines negative changes as improvement, both treatment means are in the direction of lower pain scores from baseline. The primary outcome analysis included only the 15 participants who completed both treatment phases. A separate functional-status result is not reported in the registry record, despite the proposal’s mention of functional status.

7. Results Posted in the Registry

• Ramelteon: mean -1.00 versus -1.10 on control; difference 0.10 (95% CI -0.94 to 1.14), standardized effect d = 0.07; z-test p = 0.850.

8. Statistical Interpretation

9. Statistical Methods Explained

The registry record reports a two-sided t-test for the comparison between ramelteon and placebo, with p > 0.05. A t-test assesses whether the observed difference in means is sufficiently inconsistent with a null difference under the test’s assumptions. A two-sided test considers differences in either direction rather than testing only for a larger or smaller mean in one prespecified direction. The registry does not provide the test statistic, degrees of freedom, exact p-value, or a confidence interval for the sponsor’s analysis.

What does a mean change represent?

The outcome is a continuous pain score, and the arm summaries are means of changes from baseline. The mean is the arithmetic average of the reported changes. A negative mean is described in the registry as improvement from baseline. The standard deviations are 1.4 for ramelteon and 1.5 for placebo. Standard deviation describes the dispersion of individual observations around a group mean; it is not the uncertainty in the mean itself. That uncertainty also depends on the number of observations and on the analysis structure.

What is the recalculated comparison?

The recalculation uses the posted means and standard deviations to produce a simple unadjusted mean difference and an associated interval and p-value. It is not the sponsor’s reported analysis. The recalculated mean difference is 0.1, and the recalculated p-value is 0.85. The reported pooled standard deviation is 1.451. These calculations use summary information and do not include unreported participant-level data or model adjustments.

In a crossover study, the same participant receives both treatments. In general, a paired analysis can use the within-participant difference, which may account for stable differences between people and may have a different standard error from an analysis treating treatment groups as independent. The posted summary-statistics recalculation does not incorporate a participant-level pairing term. The within-person covariance and details of any crossover model are not reported in the registry record, so the recalculation cannot reproduce an analysis that depends on those features.

Why does the discrepancy matter?

The registry record indicates a discrepancy between the sponsor analysis and the recalculation. The recalculated p-value is 0.85, whereas the sponsor reports p > 0.05. The sponsor’s own analysis takes precedence. The recalculation remains useful as a transparent, unadjusted check of the posted summary values, but it should not be treated as the trial’s definitive inferential result. The sponsor’s analysis is not accompanied by an effect estimate or confidence interval in the record, so its magnitude and precision cannot be assessed directly from that report.

What does a confidence interval communicate?

In general, a confidence interval describes a range of estimates compatible with the observed data under a specified statistical method. It is not a probability statement that the true effect lies within the particular interval. The recalculated interval includes zero, which corresponds to no difference between treatment means, and also includes values on either side of zero. This indicates that the posted summaries do not pin down a precise treatment contrast. Because it is recalculated and unadjusted, the interval is not a substitute for an interval from the sponsor’s crossover analysis.

What assumptions are not available?

The registry record does not report the original sample-size justification, interim analyses, or a complete statistical analysis plan. It also does not report whether the sponsor adjusted for treatment sequence or period, how missing outcomes were handled, or whether any distributional checks were performed. These details can affect how an analysis is interpreted, but their absence does not permit assumptions about what the investigators did. The two-sided test and reported p-value are the available description of the sponsor’s inferential analysis.

For continuous outcomes, a t-test commonly relies on assumptions about the sampling distribution of the mean and the variance structure appropriate to its design. In general, severe skewness, influential observations, or variance differences can affect inference. A crossover design adds the importance of within-participant dependence and possible period or sequence effects. The registry record does not report diagnostics or methods addressing these issues. No conclusion about whether assumptions were met can be drawn from the group means and standard deviations alone.

Only one primary outcome and one analysis are listed, and no secondary outcomes are posted. The record does not say whether additional analyses were planned or whether any multiplicity adjustment was considered. A single listed analysis limits the number of posted statistical claims, but it does not establish that no other analyses were performed. That information is not reported in the registry record.

10. Confidence Intervals and Precision

The recalculated mean difference is 0.1, with a confidence interval extending from a negative value to a positive value and including zero. The interval therefore allows for effects in either direction, as well as no difference. Its breadth relative to the point estimate signals limited precision: the posted summary data do not identify a narrow range of plausible treatment differences. The recalculated p-value is 0.85, but that value does not measure the probability that the treatments are the same or that the observed finding occurred by chance.

A confidence interval is useful because it shows both the estimate and its uncertainty. In general, a narrower interval indicates greater precision, while a wider interval indicates that the data are compatible with a broader range of effects. Here, the estimate is close to zero and the interval includes zero. The interval is a recalculation from summary statistics, not an interval reported by the sponsor, and the registry record flags a discrepancy. The sponsor’s analysis takes precedence.

The analysis included 15 participants who completed both treatment phases. Although the registry reports enrollment of 23, no interval or sensitivity analysis addressing missing outcomes is posted. The precision of the reported comparison therefore pertains to the analyzed completers and does not account for uncertainty about the participants without complete outcome data. In a crossover study, the precision can also depend on within-participant correlation, which is not reported in the registry record. The unadjusted interval cannot show how a paired analysis would change the uncertainty.

11. 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 event counts. They are planning illustrations based on the observed effect, not the trial’s original design assumptions. The listed assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the planned number of participants per arm under the stated assumptions for a design with an 80% chance of detecting the chosen effect if that effect is real. The 90% power column uses a higher target chance of detection and therefore requires more participants per arm for each listed effect. Power is a property of a planned design under specified assumptions; it is not a measure of whether the observed result is true.

The illustration uses 100%, 75%, and 50% of the observed effect. For 100% of the observed effect, the figures are 3,305 participants per arm for 80% power and 4,424 participants per arm for 90% power. For 75% of the observed effect, they are 5,875 and 7,865 participants per arm, respectively. For 50% of the observed effect, they are 13,218 and 17,695 participants per arm, respectively. Smaller effects need more participants to detect under the same assumptions, which is why the figures rise as the assumed effect becomes smaller.

These are planning illustrations, not observed power. They are computed from the observed effect and should not be read as a recommendation or as evidence that a trial of any particular size would produce a specific result. The original design rationale and assumptions are not reported in the registry record.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.100; pooled standard deviation σ = 1.451.
2. n = 2 × (1.96 + 0.842)² × 1.451² / 0.100² = 3,304.4, rounded up to 3,305 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 <- 0.1                      # observed difference in means
sigma <- 1.45086181285469                     # 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(753623)
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 = 3,305 (80% power), 4,424 (90% power)
 75% of observed effect: n per arm = 5,875 (80% power), 7,865 (90% power)
 50% of observed effect: n per arm = 13,218 (80% power), 17,695 (90% power)
power.t.test: 3305.3 
Simulated power at n = 3,305 per arm: 0.799 (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.

13. Analyses Reported by the Sponsor

The sponsor’s posted result is a two-sided t-test with p > 0.05. The record does not provide the sponsor’s effect estimate, confidence interval, or exact p-value. A separate recalculation from the posted group summaries gives a mean difference of 0.1, a confidence interval that includes zero, and p = 0.85. The registry record marks a discrepancy, so the sponsor’s own analysis takes precedence.

The recalculation is a simple unadjusted check based on the means and standard deviations in the record. It is not a reconstruction of the sponsor’s full analysis. In particular, the record does not say whether the sponsor’s t-test used the crossover pairing or accounted for sequence or treatment period. Participant-level data and the details needed to evaluate those possibilities are not reported in the registry record.

Both reports indicate a result that is not statistically significant at conventional thresholds, but the numerical p-values are not interchangeable. The sponsor’s result is the trial’s posted analysis; the recalculation is supplementary and cannot resolve why the reported values differ. The registry record does not explain the discrepancy.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome measure and one analysis. It does not post secondary outcome results; the number of secondary outcomes posted is zero. The proposal mentions improvement in functional status, but a functional-status result is not reported in the registry record. It is not possible to determine from the record whether other outcomes were planned, measured, or analyzed but not posted.

Multiplicity arises when several outcomes, time points, treatment contrasts, or analyses are tested. In general, conducting many statistical tests can increase the chance of at least one apparently unusual result, and prespecified multiplicity methods can address that issue. The registry record does not report a multiplicity plan or say whether any adjustment was made. Since only one primary analysis is listed, there is no basis in the posted record for calculating or describing an adjustment.

The primary analysis population is explicitly limited to the 15 participants who completed both treatment phases. Enrollment was 23. The registry record does not report the number of participants who failed to complete each phase, reasons for noncompletion, outcomes for those participants, or whether additional missing-data methods were used. It also does not report an analysis of all randomized participants or sensitivity analyses exploring the consequences of missing outcome data.

These omissions matter because an analysis restricted to completers may differ from an analysis that includes all randomized participants, especially if completion is related to treatment response or other participant characteristics. That possibility is a general concern, not a claim about why participants did not complete this trial. The registry record does not provide enough information to evaluate the direction or size of any potential bias.

For a crossover study, the analysis population and treatment sequence can also affect interpretation. The record does not report the numbers analyzed by sequence, the handling of period effects, or whether the comparison accounted for repeated observations within participants. These details, along with the missing-data approach and any multiplicity plan, are not reported in the registry record.

15. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: hospitalization (4.3%).

The adverse-event summaries list 23 participants at risk for serious adverse events in each treatment group. One participant is listed as affected in the ramelteon group and zero in the placebo group. For other adverse events, zero affected participants are listed in each group. The registry record also lists Hospitalization at 4.3% among the top serious terms, but it does not state in that summary which treatment group the term belongs to.

These figures should be read as the posted counts, not as proof that an event was caused by a treatment. The crossover design means participants could receive both interventions, but the registry summary does not explain how the adverse-event risk counts or event attribution were handled across treatment periods. The relationship between the 23 participants at risk in each group and the 15 participants in the primary outcome analysis is not explained in the adverse-event summary.

Deaths are not reported in the registry record. The record does not provide event descriptions, timing, severity details beyond the serious classification, or an assessment of relatedness for the serious event. The small number of posted serious events and the absence of further attribution details limit comparisons between treatment conditions.

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

The posted results show similar mean changes in the pain score under ramelteon and placebo among the participants who completed both treatment phases: -1.0 and -1.1, respectively. The registry defines negative changes as improvement from baseline. The unadjusted recalculated difference is 0.1, and its interval includes zero. The sponsor reports p > 0.05. Taken together, the posted results do not establish a statistically significant difference between treatment conditions in the sponsor’s analysis.

A result that is not statistically significant does not prove that the treatments have identical effects. It can reflect a small difference, substantial variability, limited information, or other features of the analysis. The recalculated interval spans effects on both sides of no difference, so the result does not precisely rule out either direction. The sponsor did not post an effect estimate or confidence interval, limiting direct assessment of the precision of its own analysis.

The observed mean changes are within-treatment changes from baseline; they do not by themselves show that treatment caused those changes. The primary comparison is the difference between treatments, and that comparison is uncertain. The record does not post a functional-status result, so the proposal’s broader statement about functional status cannot be assessed from the available outcomes.

The primary analysis used 15 completers, despite enrollment of 23. Missing outcomes, the reason for termination, and details of the sponsor’s crossover analysis are not reported in the registry record. Those limitations constrain how broadly the result can be interpreted. The results describe the posted pain-score analysis; they do not establish a clinical recommendation or a definitive conclusion about the effects of either intervention.

17. Why This Trial Matters Statistically

This trial is statistically notable because it combines a crossover design with a small analyzed population and a primary outcome summarized as change from baseline. In a crossover design, participants receive both treatments, which can permit a within-person comparison. Such a comparison depends on the relationship between repeated observations from the same participant. The registry record does not report whether the sponsor’s test incorporated that pairing, leaving an important feature of the analysis unclear.

The contrast between enrollment of 23 and an analysis population of 15 completers also highlights the importance of defining analysis populations and reporting missing data. Without information about noncompletion or outcomes for participants who did not complete both phases, readers cannot evaluate how the analyzed group relates to everyone enrolled. This is a general interpretive concern, not an assumption about why participants did not complete the study.

The sponsor’s result and the recalculation also illustrate why a posted p-value should be read alongside an estimate and its precision. The sponsor reports only p > 0.05, while the unadjusted recalculation gives an estimate and interval from summary data. Because the registry flags a discrepancy, the sponsor’s analysis takes precedence, but the missing sponsor estimate and interval leave its magnitude and precision less transparent.

Finally, the planning illustration demonstrates how sample-size requirements depend on the effect chosen for detection and the desired power. It is not evidence about the trial’s actual power or original planning. The original design assumptions are not reported in the registry record, and the illustration should not be confused with observed study performance.

18. Limitations

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

The registry record identifies the trial as terminated but does not report why it was terminated. It also does not provide a detailed account of treatment duration, phase timing, washout arrangements, or the handling of sequence and period effects. These details are important for assessing a crossover trial, but their absence does not establish that any particular design feature was missing or handled incorrectly.

The primary outcome analysis includes only 15 participants who completed both phases, compared with enrollment of 23. Reasons for noncompletion, outcomes for those without complete data, and analyses addressing missingness are not reported in the registry record. The posted record therefore does not allow assessment of how missing outcomes may have affected the comparison.

The sponsor’s statistical result is limited to a two-sided t-test with p > 0.05. The sponsor’s estimate, confidence interval, exact p-value, and details of the model are not reported in the registry record. The unadjusted recalculation is not a substitute for that analysis, particularly because the record marks a discrepancy and the recalculation does not use participant-level crossover information.

The record lists a proposed interest in functional status, but no secondary outcome results are posted. The adverse-event summary does not clarify attribution across the crossover periods, and deaths are not reported. The original sample-size justification, interim analyses, and full statistical analysis plan are also not reported in the registry record. Together, these gaps limit assessment of the analysis choices, missing data, safety attribution, and the scope of the conclusions.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clinical Management of Neuropathic Pain With Ramelteon — NCT00753623.
• Registry record last updated 2017-05-15; status last verified 2017-04.
• Results first posted 2014-07-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT00753623 is a randomized, triple-masked crossover study of ramelteon and placebo for neuropathic pain. The registry lists enrollment of 23 and a terminated status. The primary outcome is change in pain on a 0-10 Visual Analog Scale, with negative changes defined as improvement from baseline.

The primary analysis includes the 15 participants who completed both treatment phases. Mean changes were -1.0 for ramelteon and -1.1 for placebo. The sponsor reports a two-sided t-test with p > 0.05. A recalculation from the posted summary statistics gives a mean difference of 0.1 and p = 0.85, but the registry marks a discrepancy; the sponsor’s own analysis takes precedence.

The record does not report the reason for termination, the original sample-size justification, or key details of the crossover analysis and missing-data handling. No secondary outcome results are posted.