The Effects of Milnacipran on Sleep Disturbance in Fibromyalgia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Effects of Milnacipran on Sleep Disturbance in Fibromyalgia (NCT01234675), a randomized phase 4 study. The primary outcome is Number of Awakenings After Sleep Onset (NAASO).

2. Clinical Question

The design makes each participant's experience across treatment periods relevant to the comparison: participants crossed over between milnacipran and placebo rather than remaining in a single assigned treatment throughout. The posted primary summary reports the mean for each treatment and a paired analysis. That structure is important when interpreting the estimates because the comparison is intended to reflect within-participant differences, not simply an independent comparison between two unrelated groups.

The registry record does not report further eligibility criteria, the exact sequence allocation, or details about how the crossover periods were ordered beyond the arm descriptions. It also does not report whether a washout period was used. Those protocol details should not be inferred from the treatment-period descriptions.

3. Trial Design

This was a Phase 4 randomized, double-blind, placebo-controlled, two-way crossover study using polysomnography. The registry record identifies the allocation as randomized, masking as double, and model as crossover. The study examined milnacipran in participants with fibromyalgia and sleep disturbance. It is marked completed, with enrollment of 19 participants.

In a crossover design, a participant receives more than one study condition in sequence. That allows the analysis to compare outcomes within the same participant, which can account for stable differences between people. The sponsor's posted primary method was a paired t test, consistent with a paired comparison. Interpretation of crossover results can also depend on sequence, period, and possible carryover effects. Whether these issues were assessed, and what methods were used for them, are not reported in the registry record.

The milnacipran arm description includes dose escalation, a 28-day treatment period, and tapering before or after crossover. The placebo description specifies a 45-day placebo period before or after crossover. The primary endpoint timeframe is 4-week maintenance treatment with milnacipran and placebo. The registry record does not explain how the differing arm-description durations relate to that primary endpoint timeframe.

Although 19 participants were enrolled, the primary outcome description says that 15 subjects completed the study, and the posted primary treatment summaries each report 15 participants. The record does not report the reasons that participants did not complete the study, how their data were handled, or whether the primary analysis included any participants who did not complete both treatment periods. Those omissions matter because a paired analysis generally depends on having the relevant observations from both periods for a participant.

The study start and primary completion are recorded as 2010-11 and 2014-02. The registry record does not report a sample-size justification, the original design assumptions, or the planned handling of interim analyses.

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 (6 Weeks)

Reasons for not completing this period:

Second Intervention (6 Weeks)

Analysis population for the primary outcome, as defined in the registry: 15 subjects completed the study

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 Number of Awakenings After Sleep Onset (NAASO), measured over 4-Week maintenance treatment with milnacipran and placebo.

The primary endpoint is Number of Awakenings After Sleep Onset (NAASO), measured in awakenings. It counts awakenings after defined sleep onset until lights on, during the 4-week maintenance treatment with milnacipran and placebo. The posted summaries are means with standard errors, and the outcome description identifies 15 subjects who completed the study.

This endpoint is used to quantify one aspect of sleep continuity: how often sleep is interrupted after sleep onset. Polysomnography can record sleep during the night, making an awakening count an objective sleep measure within the study's stated assessment approach. The endpoint captures only one dimension of sleep, however. It does not by itself describe sleep quality, time taken to fall asleep, total sleep duration, fatigue, or the broader impact of fibromyalgia.

In general, a mean gives the average observed value in a group, while a standard error describes the estimated uncertainty in that mean. The standard errors reported for the treatment summaries are 4.5 for milnacipran and 4.2 for placebo. The registry record does not report additional measurement details, such as the operational rules for distinguishing an awakening or how missing recordings were handled.

The primary comparison is a paired difference, so the treatment contrast concerns the change between the milnacipran and placebo periods for participants with paired observations. The registry record identifies this as the principal endpoint but does not report a clinically meaningful threshold for interpreting the size of a difference in awakenings.

7. Results Posted in the Registry

• Milnacipran: mean 39.50 versus 34.90 on control; difference 4.60 (95% CI -7.46 to 16.66), standardized effect d = 0.27; z-test p = 0.455.

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.

Latency to Persistent Sleep Onset (LPS)

• 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:
  • Milnacipran: mean 41.60 versus 38.60 on control; difference 3.00 (95% CI -13.64 to 19.64), standardized effect d = 0.13; z-test p = 0.724.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Milnacipran and the control. The interval gives the range of effects that remain compatible with the data.

Total Sleep Time (TST)

• 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:
  • Milnacipran: mean 361.70 versus 386.10 on control; difference -24.40 (95% CI -69.96 to 21.16), standardized effect d = -0.38; z-test p = 0.294.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Milnacipran and the control. The interval gives the range of effects that remain compatible with the data.

Arousal Index (AI)

• 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:
  • Milnacipran: mean 30.20 versus 31.20 on control; difference -1.00 (95% CI -9.95 to 7.95), standardized effect d = -0.08; z-test p = 0.827.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Milnacipran and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several aspects of sleep and health, including latency to persistent sleep onset, total sleep time, arousal index, slow wave sleep, sleep-problem and sleep-quality measures, fatigue, and fibromyalgia impact. The posted numeric comparisons include the first three of those measures. Across those available comparisons, estimates do not point uniformly in one direction, and their confidence intervals include zero. This mixed pattern does not provide a clearly consistent secondary signal alongside the primary result.

The secondary outcomes are relevant as context because sleep disturbance is multidimensional: an awakening count does not capture all aspects of sleep, fatigue, or fibromyalgia impact. At the same time, secondary measures answer distinct questions and should not be treated as interchangeable confirmations of the primary endpoint. The registry record identifies 10 secondary outcomes as posted, but numeric details for the other secondary outcomes are not reported in the registry record.

Unadjusted secondary results carry less weight when many outcomes are examined. In general, repeated testing increases the chance that at least one comparison will appear unusual by chance. A prespecified hierarchy or multiplicity adjustment can help address that issue, but whether either was used is not reported in the registry record. The secondary findings should therefore be treated as exploratory context rather than independent proof of a treatment effect.

The primary outcome remains the stated principal question. Secondary outcomes can help reveal whether observations across related domains cohere, but they cannot repair imprecision in the primary estimate or establish a clinically important effect when such a threshold is not reported. The available secondary results are best read with their estimates and confidence intervals, with due attention to the number of outcomes and the incomplete reporting of numeric results.

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

• Latency to Persistent Sleep Onset (LPS)
• Total Sleep Time (TST)
• Arousal Index (AI)
• Slow Wave Sleep (SWS)
• Sleep Problem Index 2, Medical Outcomes Study Sleep Scale (MOS-SS)
• Sleep Quality Scale
• Fatigue Severity Scale (FSS) Total Score
• Fibromyalgia Impact Questionnaire (FIQ) Total Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result is a comparison of means for a continuous outcome. In general, a continuous measure can take values along a scale rather than belonging only to distinct categories. Here, the measure is the number of awakenings after defined sleep onset until lights on. The treatment summaries report the mean and standard error for each period: 39.5 with standard error 4.5 for milnacipran, and 34.9 with standard error 4.2 for placebo.

The registry record identifies a paired t test as the sponsor's method for the primary comparison. A paired test is designed for measurements linked within the same participant, such as observations under two treatment conditions in a crossover study. Rather than treating the treatment groups as unrelated samples, it analyzes within-participant differences. In general, pairing can remove some between-person variability when observations from the same person are correlated. The paired test's interpretation depends on its assumptions, including the distribution of the paired differences; the registry record does not report diagnostic checks or alternative analyses.

The recalculated mean difference is 4.6 awakenings, with a 95% confidence interval from -7.465 to 16.66 and an unadjusted p-value of 0.455. This recalculation is an unadjusted comparison based on the posted summary statistics. It is not the same analysis as the sponsor's paired test, because the posted summary statistics do not include the individual paired observations or the variability of their within-participant differences. The registry record also reports the sponsor's paired result separately.

In general, a confidence interval gives a range of values compatible with the data and the method used, while reflecting sampling uncertainty. A 95% confidence interval is not a statement that there is a 95% probability that the fixed treatment effect lies within this particular calculated interval. Its usual repeated-sampling interpretation concerns the performance of the interval procedure over repeated studies under its assumptions. The interval for the primary recalculation includes zero, as does the sponsor's reported interval.

A p-value is a measure calculated under a specified null hypothesis and statistical model. It indicates how unusual data at least as discordant with that null would be if the null and model assumptions held. It is not the probability that the null is true, and it does not quantify clinical importance. The registry record reports p = 0.424 for the sponsor's paired primary test, while the unadjusted recalculation gives p = 0.455. These values come from different approaches to the available data and should be read alongside the estimates and confidence intervals, not as stand-alone verdicts.

The registry record lists continuous outcomes summarized as means with standard errors. A standard error is the estimated sampling variability of an estimated mean; it is not the standard deviation of individual participant values. In general, a standard deviation describes variation among observations, whereas the standard error describes uncertainty in an estimated summary. The record does not provide individual-level data for assessing outcome distributions, or explain whether the reported standard errors reflect the crossover pairing.

The study's crossover design creates further statistical considerations. In general, period effects occur when outcomes differ by treatment period for reasons unrelated to the assigned treatment, and carryover occurs when an earlier treatment influences observations in a later period. Sequence may also matter if treatment order is associated with outcome patterns. The paired comparison alone does not establish how these features were addressed. The registry record does not report analyses of period, sequence, or carryover effects, nor details of any washout procedure.

There are 13 outcome measures and 13 analyses listed in the record, and 10 secondary outcomes are identified as posted. Multiple outcomes create a multiplicity issue: as the number of statistical comparisons increases, the chance of at least one apparently unusual result can rise even when there is no underlying effect. In general, adjustment methods or a prespecified hierarchy can help control how findings are interpreted. The registry record does not report whether such a strategy was planned or used. The posted p-values for the secondary measures should therefore be understood as unadjusted unless otherwise stated in the record.

Sample-size figures based on observed effects are planning illustrations, not evidence of how well this study was powered after completion. In general, a power calculation estimates the sample size needed to detect a specified effect under stated assumptions. The original trial's sample-size justification and design assumptions are not reported in the registry record. The separate illustration uses the observed effect and stated planning assumptions; it should not be interpreted as observed power or as proof that the study could or could not detect a clinically meaningful effect.

Finally, the reported primary analysis population is described as 15 subjects who completed the study. The registry record does not report a detailed analysis-population definition, how participants without complete crossover observations were handled, or whether sensitivity analyses were performed. Those details are important for assessing possible bias from incomplete follow-up.

11. Confidence Intervals and Precision

Precision is reflected most directly by the width of a confidence interval. The sponsor's primary paired estimate is 4.6 awakenings, with a 95% confidence interval from -7.3 to 16.6. The unadjusted recalculation gives the same point estimate, 4.6, with a 95% confidence interval from -7.465 to 16.66. Both intervals include zero and allow for a range of possible contrasts in either direction.

In general, a confidence interval combines a point estimate with information about its uncertainty under a statistical model. A narrower interval indicates more precise estimation under that model; a wider interval indicates greater uncertainty. Here, the primary interval is wide enough that the exact size and direction of the treatment contrast remain uncertain. It does not establish that the two treatment periods had identical means, nor does it establish a particular nonzero difference.

The recalculated and sponsor-reported intervals are close but not identical. This can occur because the recalculation uses unadjusted summary-statistic methods while the sponsor reports a paired test. The participant-level pairing can affect the estimated uncertainty, and that information cannot be recovered fully from separate treatment means and standard errors. The registry record does not report the paired-difference standard deviation or participant-level observations, so the recalculated interval should be read as a supplementary unadjusted estimate, not as a replacement for the sponsor's paired analysis.

The primary endpoint summaries are based on 15 participants who completed the study. A small completed sample can leave substantial uncertainty, but the registry record does not report the sample-size justification or the original precision target. The interval communicates uncertainty in the estimated contrast; it does not account for every potential source of bias or uncertainty, including missing data or unreported crossover effects.

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 planning illustration assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It uses the observed effect as its starting point and considers detecting the stated fraction of that observed effect. The trial's own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column indicates the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect and model were correct. The 90% power column uses the same idea with a higher target chance of detection. These are planning targets, not guarantees; actual results depend on the true effect, variability, study conduct, and analysis assumptions.

The rows for 100%, 75%, and 50% of the observed effect represent progressively smaller effects to detect. Smaller effects are harder to distinguish from random variation, so the planning illustration requires more participants per arm for those rows. These figures are not the sample size that the trial enrolled, and they do not reveal the rationale for the trial's enrollment.

This is not observed power. Observed power is not a useful substitute for interpreting the estimate and its confidence interval after a study; the planning numbers instead show how assumed effect size and target power relate to a hypothetical sample-size requirement. The calculations are presented as an illustration based on the observed effect, rather than a reconstruction of the trial's own design.

The registry identifies a crossover trial, whereas the stated planning assumptions describe equal allocation between two arms. The illustration should therefore be understood in the terms of its stated assumptions, not as a design-specific reconstruction of the crossover protocol. The registry record does not report the original calculation method or assumptions for planning enrollment.

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 = 4.600; pooled standard deviation σ = 16.857.
2. n = 2 × (1.96 + 0.842)² × 16.857² / 4.600² = 210.8, rounded up to 211 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 <- 4.6                      # observed difference in means
sigma <- 16.8574909165036                     # 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(1234675)
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 = 211 (80% power), 283 (90% power)
 75% of observed effect: n per arm = 375 (80% power), 502 (90% power)
 50% of observed effect: n per arm = 844 (80% power), 1,129 (90% power)
power.t.test: 211.8 
Simulated power at n = 211 per arm: 0.807 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor's posted primary result is a paired t test of the treatment-period difference. It reports a paired difference of 4.6 awakenings, a 95% confidence interval from -7.3 to 16.6, and p = 0.424. The unadjusted recalculation from the posted summary statistics also estimates a mean difference of 4.6, but gives a 95% confidence interval from -7.465 to 16.66 and p = 0.455.

The two approaches agree on the point estimate but do not produce exactly the same interval or p-value. The sponsor's method uses the paired structure of the crossover data. The recalculation uses unadjusted summary statistics and cannot reproduce all information about within-participant differences. It is therefore a check based on posted summaries, not a substitute for the sponsor's reported paired analysis.

The registry record does not identify a discrepancy between the recalculation and sponsor's result. The sponsor's reported analysis remains the direct record of the trial's paired test, while the recalculation offers a transparent, approximate comparison from the posted summaries. Both intervals include zero, and both indicate uncertainty around the estimated contrast. Neither p-value alone conveys the clinical importance of the difference.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 13 outcome measures and 13 analyses, and identifies 10 secondary outcomes as posted. Testing multiple outcomes raises the general issue of multiplicity: with more comparisons, the chance of at least one apparently notable result can increase even when the underlying effects are absent. A statistical plan may address this through adjustment, a hierarchy of endpoints, or a clear distinction between confirmatory and exploratory analyses. Whether any of these approaches was planned or used is not reported in the registry record.

The primary outcome is identified, but the record does not report a full statistical analysis plan, the prespecified order of tests, or how the family of secondary comparisons was defined. The posted secondary p-values should not be treated as multiplicity-adjusted because no such adjustment is reported. The record also does not report whether interim analyses were planned or performed.

Missing-data handling is also not reported. The primary outcome description states that 15 subjects completed the study, while enrollment was 19. The record does not give reasons for noncompletion, describe whether missing measurements were imputed, or say how participants with incomplete data contributed to analyses. The primary treatment summaries report 15 participants in each period, but those summaries alone do not explain the handling of any missing observations or confirm the precise analysis population.

The registry record does not report whether the analysis followed an intention-to-treat principle, a per-protocol definition, or another population rule. It also does not report sensitivity analyses for missing data. These omissions limit evaluation of whether completion and missingness could have affected the comparison.

For a crossover study, period, sequence, and carryover considerations can affect interpretation. The paired t test is reported, but further information about those potential effects is not reported in the registry record. The absence of that detail is not evidence that the issues were ignored; it means the public record does not establish how they were handled.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: gall stones (5.3%).

The registry lists serious adverse events in 0 of 19 participants at risk in the milnacipran group and 1 of 19 at risk in the placebo group. Gall Stones is the listed top serious-event term, at 5.3%. The registry record does not clearly assign that listed term to a treatment group in the serious-event summary, so it should not be attributed to one arm based on this information alone.

Other adverse events are reported in 12 of 19 participants at risk with milnacipran and 10 of 19 at risk with placebo. These counts describe participants with reported events, not the total number of events or their severity, duration, or relationship to treatment. The record does not report death counts.

In general, adverse-event counts in a small study are descriptive and may be too limited to characterize uncommon events or compare risks precisely. The registry record does not provide further details about event definitions, collection methods, seriousness assessment, or causal attribution. The figures should therefore be read as recorded safety information rather than evidence that an event was caused by or prevented by either treatment.

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

The posted results show a primary mean difference of 4.6 awakenings, with a confidence interval that includes zero and extends in both directions. The sponsor's paired analysis and the unadjusted recalculation both leave substantial uncertainty about the direction and size of the contrast. The result is a description of the completed participants and the analyses recorded, not a definitive statement about treatment effects in all people with fibromyalgia.

In general, a nonzero point estimate does not by itself establish that a difference is real, important, or attributable to treatment. The confidence interval communicates uncertainty under the analysis assumptions, while the p-value addresses compatibility with a null comparison under a specified model. Neither supplies a clinical importance threshold. The registry record does not report such a threshold for the number of awakenings.

The trial's randomized, double-blind crossover design is intended to compare treatment periods while reducing some potential sources of bias. However, the record does not report enough detail to assess all features of the crossover analysis, including sequence, period, carryover, and incomplete observations. Those limitations matter when judging how broadly to interpret the estimate.

Nor should the primary result be treated as a complete account of sleep or fibromyalgia. The endpoint measures awakenings after sleep onset, while secondary outcomes address other sleep measures, fatigue, and impact. The available numeric secondary results do not show a uniformly aligned pattern, and the multiplicity plan is not reported. The broader secondary outcome results are not reported in the registry record.

Thus, the posted data support a cautious reading: they quantify the observed treatment-period contrast among study completers and show that it is imprecisely estimated. They do not establish benefit, harm, equivalence, or absence of an effect. More detailed protocol and analysis information would be needed to assess potential bias and the extent to which these findings apply beyond the recorded study population.

18. Why This Trial Matters Statistically

This trial illustrates why design details and analysis methods matter alongside a point estimate. A crossover study is naturally paired: the same participant contributes observations under different conditions. The sponsor's paired t test reflects that structure, while a recalculation from treatment means and standard errors cannot fully recover the within-participant variability. The two approaches therefore provide related but not identical uncertainty estimates.

The example also shows the distinction between an estimated effect and its precision. The mean difference is 4.6 awakenings, but its 95% confidence interval includes values below and above zero. A point estimate alone would conceal that uncertainty. Reading the interval and the reported paired analysis together gives a more complete account of what the study can establish statistically.

The completed sample was 15 participants, despite enrollment of 19. The public record does not detail noncompletion or missing-data handling. In a paired design, complete observations across treatment periods are particularly relevant, so understanding who contributed to the analysis is part of interpreting the result, not just administrative detail.

Multiplicity is another central issue: the study records numerous outcome measures and secondary comparisons. Sleep is a set of related but distinct domains, so examining several outcomes can be informative, but unadjusted findings require restraint. The record's missing details about any hierarchy or adjustment make it especially important not to elevate isolated secondary results over the primary question.

Finally, the planning illustration emphasizes that required sample size depends on the effect one wants to detect and the desired chance of detecting it under assumptions. It is separate from the trial's own design rationale, which is not reported. Together, these features make the study a useful example of interpreting paired estimates, uncertainty, incomplete reporting, and multiple outcomes without treating a single p-value as the whole result.

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 analysis is based on 15 subjects who completed the study, while enrollment was 19. The registry record does not report why participants did not complete the study, whether they provided partial outcome data, or how missing observations were handled. This limits assessment of whether the analyzed participants differed from those who did not complete the study.

The public record reports a paired t test but does not report the distribution of paired differences, diagnostic checks, or sensitivity analyses. It also does not report whether sequence, period, or carryover effects were evaluated, or whether a washout period was used. These details are particularly relevant to a crossover design; their absence from the record does not establish that the issues were not addressed in the study.

The treatment descriptions include a 7-day dose escalation, 28-day milnacipran treatment, a 7-day taper, and a 45-day placebo period, while the primary timeframe is described as 4-week maintenance treatment. The registry record does not explain how the arm durations relate to the primary endpoint timeframe or give further detail about assessment timing.

The study has several outcomes, but multiplicity handling and the prespecified analysis hierarchy are not reported. Numeric results for all listed secondary measures are not reported in the registry record. The trial's sample-size justification, original design assumptions, analysis-population definition, and interim-analysis plan are also not reported. These gaps limit appraisal of precision, selective reporting, and the robustness of the conclusions.

Finally, the registry record does not give a threshold for a clinically meaningful difference in awakenings. Statistical uncertainty can be described from the confidence interval, but the practical importance of the point estimate cannot be determined from the posted results alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: The Effects of Milnacipran on Sleep Disturbance in Fibromyalgia — NCT01234675.
• Registry record last updated 2019-08-21; status last verified 2019-08.
• Results first posted 2015-07-22.
• 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

NCT01234675 is a completed Phase 4 randomized, double-blind, placebo-controlled, two-way crossover polysomnography study of milnacipran for sleep disturbance in fibromyalgia. Enrollment was 19, and the primary outcome description states that 15 subjects completed the study.

The primary outcome was mean Number of Awakenings After Sleep Onset during 4-week maintenance treatment. The posted means were 39.5 with milnacipran and 34.9 with placebo. The sponsor reported a paired difference of 4.6, a 95% confidence interval from -7.3 to 16.6, and p = 0.424. The unadjusted recalculation gives a 95% confidence interval from -7.465 to 16.66 and p = 0.455.

The results are imprecise, and the registry record does not report important details about missing-data handling, crossover effects, multiplicity, or the trial's original sample-size justification. Safety counts are descriptive and do not establish causation.