Study of Milnacipran in Patients With Inadequate Response to Duloxetine for the Treatment of Fibromyalgia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Milnacipran in Patients With Inadequate Response to Duloxetine for the Treatment of Fibromyalgia (NCT01077375), a randomized phase 4 study. The primary outcome is Responder Status Based on Patient Global Impression of Change (PGIC) Score at Visit 5 (Week 13).

2. Clinical Question

The study’s stated objective was to evaluate the safety, tolerability and efficacy of milnacipran in this population. The primary outcome focused on patients’ own assessment of change in pain sensation and quality of life, rather than a clinician-rated measure. The registry record also reports a secondary outcome concerning change in a one-week pain-recall score from baseline to Visit 5.

The treatment comparison should be read in the context of the study population and its response definition. It addresses the recorded outcomes among patients with an inadequate response to duloxetine, not all patients with fibromyalgia. The posted results do not establish what would happen in other populations or under other treatment conditions.

3. Trial Design

This was a Phase 4, randomized, parallel-group, placebo-controlled study sponsored by Forest Laboratories. The registry record lists the study as completed, with a start date of 2010-02 and primary completion in 2010-12. Enrollment was 107. The study title describes a multicenter, double-blind switch study; the registry record lists quadruple masking.

Participants were assigned to milnacipran or placebo. The milnacipran regimen was 100 to 200 mg/day by mouth, twice daily in divided doses. The placebo regimen was oral tablets twice a day. The registry record does not report the number assigned to each treatment for the overall study enrollment in the same way as the primary-outcome analysis populations, so the outcome-specific denominators are the relevant figures when interpreting the posted results.

The primary endpoint was responder status based on the Patient Global Impression of Change (PGIC) at Visit 5 (Week 13). The registry describes assessments at Visit 4 (Week 9) and Visit 5 (Week 13), or at early termination, and says the presented results used a last-observation-carried-forward (LOCF) approach. The reported primary-outcome arms contain 21 placebo patients and 79 milnacipran patients; these are the analysis denominators attached to that outcome.

The secondary outcome was change from baseline (Week 3) to Visit 5 (Week 13) in the Visual Analog Scale (VAS) one-week pain-recall score. That result has outcome-specific denominators of 21 for placebo and 79 for milnacipran. The registry record lists two outcome measures but has one secondary outcome posted. It does not report a detailed protocol, the original sample-size justification, or the full statistical analysis plan.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: All participants were given an open-label treatment of duloxetine 60 mg once daily for a two week period before randomization. Patients randomized to placebo received 1 week of duloxetine 30 mg to effect a duloxetine down-taper. Patients randomized to milnacipran received 1 week of placebo capsules to maintain the blind.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT Population: patients in the Double-blind Safety Population with ≥ 1 PGIC post-baseline assessment. Double-blind Safety Population includes 6 patients who were not included in ITT population. Presented results generated via LOCF approach. No statistical comparisons between groups are presented; study was exploratory, not hypothesis-testing.

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 Responder Status Based on Patient Global Impression of Change (PGIC) Score at Visit 5 (Week 13), measured over Assessed at Visit 4 (Week 9) and Visit 5 (Week 13) or early termination. Presented results generated via LOCF approach..

The primary endpoint is the number of participants classified as responders on the Patient Global Impression of Change (PGIC) at Visit 5 (Week 13). The PGIC is a patient-reported rating of improvement in pain sensation and quality of life, with scores ranging from 1 (very much improved) to 7 (very much worse). For this study, a response required a score of 1 or 2: very much improved or much improved.

A responder definition turns a graded patient report into a yes-or-no outcome. This makes it possible to compare the number meeting a prespecified improvement threshold across treatment groups, while retaining a direct link to patients’ reported experience. It also means that the result depends on the chosen cutoff: people just outside the responder definition are counted with those reporting no improvement or worsening, even though their individual experiences may differ.

The registry record says the endpoint was assessed at Visit 4 (Week 9) and Visit 5 (Week 13), or early termination, and that results were presented using LOCF. The primary outcome is therefore a count of responders under that recorded analysis approach, not a continuous measure of the degree of change. The registry record states that no statistical comparisons between groups are presented for this outcome, so the counts and the unadjusted recalculation should be distinguished from a sponsor-reported inferential analysis.

7. Results Posted in the Registry

• Milnacipran: 32.9% (26/79) versus 23.8% (5/21) on control; risk difference 9.1 percentage points (95% CI -11.9 to 30.1), risk ratio 1.38 (0.60–3.16); unadjusted two-proportion z-test p = 0.423.

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 Visit 5 (Week 13) in the Visual Analog Scale (VAS) 1-week Pain Recall Score

• 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:
  • Milnacipran: mean -12.30 versus -1.30 on control; difference -11.00 (95% CI -22.35 to 0.35), standardized effect d = -0.42; z-test p = 0.058.
• 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 registry record posts one secondary outcome: change from baseline in the VAS one-week pain-recall score. The mean changes and their comparison are a continuous-outcome perspective alongside the primary endpoint’s responder count. These outcomes capture different aspects of the data: one records average change on a scale, while the other classifies patients using a PGIC threshold.

The secondary comparison’s direction is consistent with a larger decrease in the milnacipran group’s mean score, but the interval crosses zero and the unadjusted p-value is 0.058. It does not provide a definitive statistical separation between groups on its own. The primary and secondary results therefore should not be treated as interchangeable confirmations: they use different measurements and different summary scales.

Unadjusted secondary results carry less weight because multiple outcomes or comparisons can increase the chance of at least one apparently notable result arising by chance. General statistical explanation: multiplicity procedures account for that broader testing context, often by changing the criteria for interpreting individual tests. The registry record does not report whether a multiplicity adjustment was planned or applied. It also lists no reported analyses for the secondary outcome.

The secondary finding can still help describe the pattern of observed results and may be useful for planning or further study. However, it should be considered exploratory in the absence of a reported analysis plan, multiplicity strategy, or sponsor-reported inferential analysis. It should not override the primary endpoint or be treated as independent proof of a treatment effect.

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

• Change From Baseline to Visit 5 (Week 13) in the Visual Analog Scale (VAS) 1-week Pain Recall Score

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary outcome count?

The primary outcome is binary at the participant level: each person is classified as a responder or not a responder according to the PGIC cutoff. The registry reports counts of participants meeting the cutoff and the outcome-specific denominator in each group. A binary outcome can be summarized as a count or as a proportion, then compared between treatment groups using a chosen effect measure. The posted comparison uses a risk difference, which expresses the contrast between the group proportions on an additive scale.

A risk difference of 0 corresponds to equal proportions under that measure. A positive estimate for the milnacipran group indicates a higher observed responder proportion than in the placebo group; a negative estimate would indicate a lower one. The estimate is descriptive of the observed comparison and does not by itself establish that treatment assignment caused the difference. Interpretation also depends on uncertainty, the analysis population, and the study design.

How should the p-value be understood?

A p-value describes how compatible the observed data are with a specified null model, using the assumptions of the test. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. A larger p-value does not establish that two groups are equivalent; a smaller one does not correct for bias or missing information.

The posted primary p-value is unadjusted. That means the result is not described as adjusted for the possibility of testing multiple outcomes or comparisons. The registry record states that no statistical comparisons between groups are presented for the primary endpoint. The displayed comparison statistics are therefore appropriately read as unadjusted recalculations from the posted summaries rather than as the sponsor’s reported inferential analysis.

What does the secondary mean difference represent?

The secondary outcome is continuous: it reports mean change in VAS one-week pain-recall score from baseline (Week 3) to Visit 5 (Week 13). A mean difference compares the average change in one group with the average change in the other. Negative within-group changes indicate decreases on the recorded scale, while the comparison estimate describes the contrast between those average changes. The standard deviation describes the spread of individual changes around each group mean; it is not the uncertainty of the mean itself.

For this outcome, the posted comparison is an unadjusted mean difference, with an unadjusted p-value. The registry record lists no reported secondary analyses. An unadjusted result can be informative as a descriptive comparison, but it should not be treated as a confirmed finding when the analysis plan and any multiplicity strategy are not reported in the registry record.

Why does over-dispersion matter for count outcomes?

General statistical explanation: for a binary endpoint, the observed number of responders varies from sample to sample. The amount of uncertainty depends on the responder proportions and the denominators. When counts are small, a few individual outcomes can have a noticeable effect on the estimate. This is one reason to read the point estimate together with its confidence interval rather than treating the observed counts as a precise measure of the underlying difference.

Over-dispersion is more commonly discussed for count models, where variation can exceed what a simple model assumes. General statistical explanation: if a model underestimates the variability in the data, its standard errors may be too small and its intervals too narrow. The registry record does not report use of a count model or a specific over-dispersion analysis for this trial; the binary responder endpoint is reported as participant counts, so no such model should be assumed.

What does LOCF imply?

LOCF means last observation carried forward. General statistical explanation: when a later measurement is missing, this approach uses the participant’s last recorded measurement as a substitute for the missing later value. It can retain participants with incomplete follow-up in an analysis, but it relies on assumptions about how the unobserved outcome relates to the last observed one. Those assumptions may not hold for every participant or outcome.

The registry record says the primary results used LOCF and describes assessments at Visit 4 and Visit 5 or early termination. It does not report the amount or pattern of missing data, the reasons for missingness, or sensitivity analyses comparing LOCF with alternative approaches. The implications of that missing-data handling therefore cannot be fully assessed from the registry record.

Which analysis populations are described?

The primary-outcome population is described as the ITT Population: patients in the Double-blind Safety Population with at least one post-baseline PGIC assessment. The registry record also says the Double-blind Safety Population includes six patients not included in the ITT population. The primary-outcome denominators shown in the posted results are 21 for placebo and 79 for milnacipran. The adverse-event denominators differ, so those safety figures should not be substituted for the primary endpoint denominators.

The registry record does not report a complete analysis-population flow or a detailed account of exclusions by treatment group. It also does not report the planned statistical model, covariate adjustments, or the original sample-size justification. Such details can influence how a treatment contrast should be interpreted and cannot be inferred from the endpoint summaries alone.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.091, but its confidence interval extends from a negative value to a positive value and includes zero. This means the observed data are compatible with uncertainty about both the direction and the size of the group difference. The interval is broad relative to the point estimate, so the estimate is not precise enough to pin down a narrow range of plausible differences.

The primary p-value is 0.423, and the registry record says no statistical comparisons between groups are presented for this endpoint. The recalculated interval and p-value should therefore be interpreted as unadjusted summaries based on the posted counts, not as a sponsor-reported primary analysis. The interval is more informative about uncertainty than a binary significant-or-not-significant label, but it still depends on the assumptions of the recalculation.

For the secondary mean difference, the posted estimate is -11.0, with a confidence interval that also crosses zero. The unadjusted p-value is 0.058. This interval likewise allows values near no difference as well as values in the direction of the point estimate; the result does not precisely determine the size of the contrast.

Confidence intervals describe a range of values compatible with the data under a statistical model and its assumptions. They do not account automatically for every limitation, such as missing-data assumptions, the choice of endpoint, or multiplicity. In this study, modest outcome-specific denominators, the primary endpoint’s defined analysis population, and the lack of detailed analysis reporting all matter when judging precision. The estimates are useful for describing what was observed, but they should not be mistaken for exact treatment 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 sample-size figures are planning illustrations expressed as participants per arm for this two-group comparison. They are not total-event counts. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original design assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true effect and the statistical model assumptions held. The 90% power column gives the corresponding planning number for a 90% chance. These are planning quantities, not guarantees about a future result, and they do not measure the probability that the observed study result is true.

The rows using 100% of the observed effect illustrate planning around the full observed estimate. Rows using 75% or 50% of the observed effect illustrate progressively smaller effects. For the primary outcome, the figures are 384 and 514 participants per arm for 80% and 90% power when planning for 100% of the observed effect; for 75%, they are 667 and 892; for 50%, they are 1,461 and 1,955. Smaller effects need more participants to detect under the same assumptions.

For the secondary outcome, the corresponding figures are 91 and 121 participants per arm for 100% of the observed effect; 161 and 216 for 75%; and 362 and 484 for 50%. These are illustrations derived from the observed estimates, not a reconstruction of the trial’s original design calculation. This is not observed power: observed power is not a useful substitute for interpreting the estimates and their uncertainty after the data have been collected.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.238; treatment proportion p₁ = 0.329; average p̄ = 0.284.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6375 = 1.2494.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6342 = 0.5338.
4. n = (1.2494 + 0.5338)² / (0.0910)² = 383.8, rounded up to 384 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
p0 <- 0.238095238095238                          # control proportion
p1 <- 0.329113924050633                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1077375)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 384 (80% power), 514 (90% power)
 75% of observed effect: n per arm = 667 (80% power), 892 (90% power)
 50% of observed effect: n per arm = 1,461 (80% power), 1,955 (90% power)
power.prop.test: 383.8 
Simulated power at n = 384 per arm: 0.801 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, or comparisons are examined. The more tests conducted, the greater the chance that at least one result will appear notable by chance, even if there is no underlying difference. General statistical explanation: a prespecified testing hierarchy or an adjustment to the testing procedure can help control that risk. The registry record does not report a multiplicity strategy for this study.

The record lists two outcome measures and one secondary outcome, with the primary endpoint assessed at Visit 4 and Visit 5 or early termination. It does not report whether both primary assessment occasions were tested, how they were prioritized, or whether results at multiple visits were incorporated into a formal testing procedure. No multiplicity-adjusted comparisons are posted. The primary results explicitly state that no statistical comparisons between groups are presented.

Missing-data handling is described for the primary endpoint: results were generated using LOCF. The record does not report the number of missing PGIC assessments, the reasons for missingness, or whether missingness differed by group. It also does not report sensitivity analyses testing alternative assumptions. LOCF can make an analysis possible when later observations are unavailable, but its validity depends on assumptions that cannot be checked from the posted summary.

The analysis population is described as the ITT Population, defined as members of the Double-blind Safety Population with at least one post-baseline PGIC assessment. The record says the Double-blind Safety Population includes six patients who were not in the ITT population. The results therefore do not represent every person in the safety population under the recorded primary analysis definition. A complete account of participant flow and reasons for exclusion is not reported in the registry record.

The original statistical analysis plan, sample-size justification, interim-analysis plan, and any prespecified handling of multiple testing are not reported in the registry record. Their absence limits assessment of whether the posted analyses align with the planned analysis. These omissions do not invalidate the descriptive results, but they call for caution when interpreting inferential claims.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypersensitivity (1.2%), suicidal ideation (1.2%).

The posted serious-adverse-event figures use safety denominators of 21 for placebo and 85 for milnacipran. Serious adverse events affected 0 participants in the placebo group and 2 in the milnacipran group. These are counts within the reported safety populations, not the primary-outcome denominators. They should be read as event summaries rather than as a complete measure of comparative safety.

The registry lists hypersensitivity and suicidal ideation among the leading serious-event terms, each reported as 1.2%. The record does not provide event-level timing, duration, severity beyond seriousness, or a comparative statistical analysis for these terms. Deaths are not reported in the registry record.

Serious adverse events are a subset of safety information. The posted counts do not by themselves describe all adverse events, establish whether an event was caused by treatment, or allow a reliable comparison of risk. The safety denominators differ from those for the primary endpoint, reflecting the different outcome populations recorded in the registry.

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

The primary result describes the number of participants who met a specific patient-reported improvement threshold at Visit 5 (Week 13). The observed counts were 5 of 21 with placebo and 26 of 79 with milnacipran. The unadjusted risk-difference estimate is 0.091, while its confidence interval includes zero and the unadjusted p-value is 0.423. Together, these quantities indicate an uncertain estimate rather than a precise determination of the treatment-group contrast.

The result does not establish that milnacipran is effective or ineffective, nor does it show that the treatments are equivalent. A failure to demonstrate a clear difference is not proof of no difference. Conversely, the positive point estimate alone is not proof of a benefit. The uncertainty interval and the limits of the analysis reporting remain central to interpretation.

The study concerned people with fibromyalgia who had an inadequate response to duloxetine, under the recorded treatment regimens and follow-up. Its results should not automatically be generalized to other populations, dosing approaches, study settings, or outcomes. The primary endpoint is a PGIC responder classification, while the secondary endpoint is change in a pain-recall scale; neither fully captures every possible outcome of interest.

The registry record says primary results were generated using LOCF and that no statistical comparisons between groups were presented for the primary endpoint. The displayed comparison statistics are unadjusted recalculations from posted summaries. The registry record does not report detailed missing-data patterns, the original sample-size rationale, or the statistical plan. Those gaps restrict how strongly the posted results can support broader claims.

Accordingly, the most defensible reading is descriptive and cautious: the groups had the reported responder counts, and the recalculated contrast remains uncertain. The findings contribute information about this trial’s outcomes but cannot alone resolve the wider question of how milnacipran compares with placebo in this population.

17. Why This Trial Matters Statistically

This trial is statistically informative because it focuses on a defined treatment question: milnacipran versus placebo among patients with fibromyalgia who had an inadequate response to duloxetine. The primary outcome uses a patient-reported responder threshold rather than relying only on an average score. That makes the result easy to relate to the study’s stated definition of improvement, while also making it sensitive to the cutoff chosen for classifying responders.

The reported risk-difference estimate offers an interpretable contrast between group proportions, but its interval includes values in both directions. The example illustrates why an effect estimate should be read alongside its precision rather than reduced to whether a p-value passes a threshold. The primary p-value is unadjusted, and the registry record says no statistical comparison between groups was presented for the endpoint.

The study also illustrates the importance of distinguishing outcome populations. The primary endpoint and safety summaries use different denominators, and the primary population is defined by availability of at least one post-baseline PGIC assessment. Treating these denominators as interchangeable would obscure which participants contribute to each result.

Finally, the secondary measure and the primary responder endpoint answer related but distinct questions. Their interpretation depends on the measurement scale, analysis choices, and multiplicity context. The registry record does not report a complete statistical plan or the original sample-size assumptions. These omissions make the trial a useful example of how much context is needed to interpret posted trial results responsibly.

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.

Several limitations are specific to the recorded outcomes and reporting. The primary comparison is based on 21 placebo participants and 79 milnacipran participants in the outcome analysis, and the confidence interval is broad enough to include differences in either direction. The registry record explicitly notes that no statistical comparisons between groups are presented for the primary endpoint; the posted inferential statistics are unadjusted recalculations from summary data.

The primary analysis uses a restricted population: the ITT Population is described as members of the Double-blind Safety Population with at least one post-baseline PGIC assessment. The registry record notes six patients in the Double-blind Safety Population who were not included in the ITT population. It does not provide a complete flow of participants or detailed reasons for this exclusion. The LOCF approach is stated, but the extent and pattern of missingness and the results of sensitivity analyses are not reported.

The safety summaries have different denominators from the primary outcome. That distinction limits direct comparison across efficacy and safety summaries and underscores the need to interpret each outcome within its own analysis population. The record does not include deaths in the posted safety information.

Only one secondary outcome is posted, and no secondary analyses are reported. The registry record does not report whether multiplicity was addressed, what the original sample-size calculation assumed, or whether interim analyses were planned. It also does not provide detailed information about the statistical model, covariate adjustment, or protocol deviations. These reporting gaps do not change the recorded counts and means, but they limit assessment of how completely the posted results reflect the intended analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study of Milnacipran in Patients With Inadequate Response to Duloxetine for the Treatment of Fibromyalgia — NCT01077375.
• Registry record last updated 2012-01-26; status last verified 2011-12.
• Results first posted 2012-01-26.
• 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

NCT01077375 was a completed Phase 4 randomized, parallel-group, placebo-controlled study sponsored by Forest Laboratories. It enrolled 107 participants and investigated milnacipran in patients with fibromyalgia who had an inadequate response to duloxetine. The registry record lists quadruple masking.

The primary outcome was PGIC responder status at Visit 5 (Week 13), with response defined as a score of 1 or 2. The posted counts were 5 of 21 for placebo and 26 of 79 for milnacipran. The unadjusted risk-difference estimate is 0.091, with an unadjusted p-value of 0.423; the registry record says no statistical comparisons between groups are presented for the primary endpoint.

One secondary outcome was change in the VAS one-week pain-recall score from baseline to Visit 5. Its comparison is uncertain, and the registry record lists no reported secondary analyses. The primary results used LOCF. The original sample-size assumptions, detailed statistical plan, and multiplicity approach are not reported in the registry record.