Treatment of Pain Associated With Fibromyalgia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Treatment of Pain Associated With Fibromyalgia (NCT02187159), a randomized phase 3 study. The primary outcome is Change From Baseline to Week 13 in Average Daily Pain Score (ADPS) in Participants Receiving DS-5565, Pregabalin, or Placebo.

2. Clinical Question

The trial asked whether change from baseline to Week 13 in average daily pain score differed among participants with pain associated with fibromyalgia who received DS-5565, pregabalin, or placebo. It was a randomized, double-blind, placebo- and active-controlled study. The primary measure was based on participants’ daily ratings of their worst pain over the previous 24 hours; those daily ratings were averaged across 7 days to form a weekly score.

The primary comparison of interest was each DS-5565 regimen versus placebo. The registry also reports an active-control arm receiving pregabalin 150 mg BID. The result therefore gives a set of arm-level changes and contrasts rather than a single comparison between DS-5565 and all other treatments. Secondary outcomes addressed participant-rated overall change, fibromyalgia impact, fatigue, anxiety and depression, health status, sleep interference, and other measures listed in the registry record.

3. Trial Design

The registry identifies this as a completed, randomized, quadruple-masked, parallel-group phase 3 study sponsored by Daiichi Sankyo. The recorded enrollment is 1270. Four groups are described: placebo, pregabalin 150 mg BID, DS-5565 15 mg QD, and DS-5565 15 mg BID. The placebo tablet and capsule were used in the arm descriptions to support matching of the different dosing schedules. The record describes the study as both placebo-controlled and active-controlled.

The primary endpoint was a continuous measure: change from baseline to Week 13 in average daily pain score. The primary analysis population is identified as the modified intent-to-treat analysis set. Arm-level results are reported as means with standard errors. The registry also lists secondary outcomes covering participant global impression of change, fibromyalgia impact, responder status, fatigue, anxiety and depression, quality of life, and sleep interference. The registry record lists 12 outcome measures and 118 analyses, while detailed outcome results are available for only a subset of the listed secondary outcomes.

The record gives the study start as 2014-11 and primary completion as 2016-07-07. It does not report the original sample-size justification, the planned statistical model for the primary endpoint, whether interim analyses were planned, or the full analysis plan. Masking and randomization describe important design features, but they do not by themselves establish how missing observations, multiplicity, or protocol deviations were handled. Those details are not reported in the registry record.

The arm sizes attached to outcome analyses can differ slightly across endpoints, and the primary outcome population is specifically described as modified intent-to-treat. These analysis denominators should be read as endpoint-specific records rather than assumed to be identical for every measure. The posted results do not explain every difference in those denominators.

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: Eligible participants were randomized in a 1:1:1:1 ratio to either DS5565 15 mg QD, DS5565 15 mg BID, placebo, or pregabalin 150 mg BID.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ADPS was assessed using the modified intent-to-treat (mITT) analysis set.

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.

Population: Demographics at baseline were assessed in the Randomized Analysis Set.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline to Week 13 in Average Daily Pain Score (ADPS) in Participants Receiving DS-5565, Pregabalin, or Placebo, measured over Baseline up to Week 13 postdose.

The primary endpoint is change from baseline to Week 13 in average daily pain score, or ADPS. Participants rated their pain intensity daily, describing the worst pain over the previous 24 hours. The scale runs from 0, no pain, to 10, worst possible pain. The daily ratings were averaged over 7 days to produce a weekly ADPS. The registry gives the timeframe as baseline up to Week 13 postdose and identifies the modified intent-to-treat analysis set for this assessment.

A change score expresses how the measured outcome at follow-up differs from its baseline value. In this setting, a negative change means the recorded score is lower at follow-up than at baseline. The group means describe average change, while a between-group mean difference describes how the average change in one arm compares with the average change in placebo. These summaries do not show how every participant’s score changed, nor do they establish that individual experiences followed the group average.

Repeated daily ratings, combined into a weekly average, provide a structured summary of reported pain over the assessment period rather than relying on one isolated daily observation. The endpoint is relevant to the trial’s stated objective because it directly uses participant-reported pain intensity. Interpretation still depends on the scale, the timing of assessments, the analysis population, and the handling of missing observations. Those details should not be inferred beyond the registry description. The registry does not report a threshold defining a clinically important change on this scale.

7. Results Posted in the Registry

• Pregabalin 150 mg BID: mean -2.47 versus -1.86 on control; difference -0.61 (95% CI -0.97 to -0.25), standardized effect d = -0.26; z-test p = 0.001.
• DS-5565 15 mg QD: mean -2.24 versus -1.86 on control; difference -0.38 (95% CI -0.74 to -0.02), standardized effect d = -0.16; z-test p = 0.041.
• DS-5565 15 mg BID: mean -2.09 versus -1.86 on control; difference -0.23 (95% CI -0.60 to 0.14), standardized effect d = -0.10; z-test p = 0.218.

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.

Number of Participants Who Answered "Much Improved or Better" on the Patient Global Impression of Change (PGIC) Scale at Week 13 in Participants Receiving DS-5565, Pregabalin, or Placebo

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Pregabalin 150 mg BID: 45.2% (141/312) versus 28.9% (91/315) on control; risk difference 16.3 percentage points (95% CI 8.9 to 23.8), risk ratio 1.56 (1.27–1.93); unadjusted two-proportion z-test p = <0.001.
  • DS-5565 15 mg QD: 36.8% (116/315) versus 28.9% (91/315) on control; risk difference 7.9 percentage points (95% CI 0.6 to 15.2), risk ratio 1.27 (1.02–1.60); unadjusted two-proportion z-test p = 0.034.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Pregabalin 150 mg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for DS-5565 15 mg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline to Week 13 in Fibromyalgia Index Questionnaire (FIQ) Total Score in Participants Receiving DS-5565, Pregabalin, or Placebo

• 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:
  • Pregabalin 150 mg BID: mean -21.46 versus -13.88 on control; difference -7.58 (95% CI -7.77 to -7.39), standardized effect d = -6.26; z-test p = <0.001.
  • DS-5565 15 mg QD: mean -17.41 versus -13.88 on control; difference -3.53 (95% CI -3.72 to -3.34), standardized effect d = -2.92; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Pregabalin 150 mg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for DS-5565 15 mg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline to Week 13 in Multidimensional Fatigue Inventory (MFI-20) General Fatigue Score in Participants Receiving DS-5565, Pregabalin, or Placebo

• 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:
  • Pregabalin 150 mg BID: mean -2.80 versus -1.40 on control; difference -1.40 (95% CI -2.00 to -0.80), standardized effect d = -0.38; z-test p = <0.001.
  • DS-5565 15 mg QD: mean -2.30 versus -1.40 on control; difference -0.90 (95% CI -1.47 to -0.33), standardized effect d = -0.26; z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Pregabalin 150 mg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for DS-5565 15 mg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The listed secondary outcomes broaden the assessment beyond weekly pain ratings. They include global impression of change, fibromyalgia impact, responder status, fatigue, anxiety and depression, health-related quality of life, and sleep interference. This range can help describe whether the primary pain measure is accompanied by changes in other reported domains, but those outcomes answer different questions and should not be treated as interchangeable with ADPS.

The detailed posted secondary results cover only part of the outcome list. Across the available comparisons, some secondary measures have reported contrasts favoring active arms over placebo under their stated analyses, while the available data do not give a complete result set for every listed endpoint. The broader pattern is therefore supportive context rather than a comprehensive, independent confirmation of the primary finding. Results for secondary outcomes not detailed in the registry record are not reported in the registry record.

Secondary findings also require particular caution because the registry lists many outcomes and analyses. If numerous hypotheses are examined, some apparently notable results can occur by chance. The registry record does not report a multiplicity strategy for the secondary analyses. The recalculated comparisons are unadjusted, and unadjusted p-values do not control the overall chance of false-positive findings across a family of tests. Confidence intervals for separate secondary outcomes likewise do not, by themselves, resolve the multiplicity issue.

The secondary outcomes are most useful as descriptive and exploratory context unless their role, analysis, and multiplicity handling are specified. They can indicate which domains were assessed and what the posted estimates suggest, but they cannot repair limitations in the primary analysis or substitute for missing results. Interpretation should keep the primary endpoint distinct from the other outcomes and avoid treating a collection of secondary comparisons as a single confirmatory conclusion.

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

• Number of Participants Who Answered "Much Improved or Better" on the Patient Global Impression of Change (PGIC) Scale at Week 13 in Participants Receiving DS-5565, Pregabalin, or Placebo
• Change From Baseline to Week 13 in Fibromyalgia Index Questionnaire (FIQ) Total Score in Participants Receiving DS-5565, Pregabalin, or Placebo
• Number of Responders at Week 13 Among Participants Receiving DS-5565, Pregabalin, or Placebo
• Change From Baseline to Week 13 in Multidimensional Fatigue Inventory (MFI-20) General Fatigue Score in Participants Receiving DS-5565, Pregabalin, or Placebo
• Change From Baseline to Week 13 in Hospital Anxiety and Depression Scale (HADS) in Participants Receiving DS-5565, Pregabalin, or Placebo
• Change From Baseline to Week 13 in Short Form 36 (SF-36) in Participants Receiving DS-5565, Pregabalin, or Placebo
• Change From Baseline to Week 13 in EuroQol Five Dimensions Questionnaire (EQ-5D) in Participants Receiving DS-5565, Pregabalin, or Placebo
• Change From Baseline to Week 13 in Average Daily Sleep Interference Score (ADSIS) in Participants Receiving DS-5565, Pregabalin, or Placebo

9. Statistical Interpretation

10. Statistical Methods Explained

What does a difference of means describe?

For a continuous outcome, a difference of means compares the average value in one group with the average value in another. In the primary analysis, the arm summaries are mean changes in ADPS, and the comparison is a mean difference. The direction depends on which group is subtracted from which. For the registry-reported placebo comparisons, negative estimates indicate a lower mean change in the active-treatment arm than in placebo under the contrast’s stated ordering. Because the outcome is a change score, interpretation should retain both the scale and the baseline-to-follow-up framing.

The arm means and their standard errors describe different features. The mean is the estimated average change. A standard error describes uncertainty in that estimated mean; it is not the spread of individual participant scores. The registry lists the primary arm results with standard errors. It does not provide standard deviations for that primary measure in the same outcome record.

What does a confidence interval add?

A confidence interval gives a range of values compatible with the observed data and the statistical method, at the stated confidence level. It communicates estimation uncertainty rather than a range containing a fixed proportion of individual participants. For the primary comparisons, the sponsor-reported intervals are 95% confidence intervals. An interval spanning zero includes no between-group mean difference among the values compatible with that interval. An interval that does not span zero is evidence of a nonzero contrast under the analysis, but does not establish clinical importance or remove concerns about multiplicity or analysis choices.

Why can recalculations differ from the reported analysis?

A simple recalculation from posted group summaries uses the displayed means, standard errors, and group sizes to form an unadjusted contrast. It can help readers understand the arithmetic implied by those summaries. It may not reproduce the sponsor’s analysis, which can use a different model, adjustment, analysis set, missing-data approach, or unrounded underlying values. The registry record does not provide enough detail to identify the reason for every discrepancy. Since a discrepancy is flagged for the primary outcome, the sponsor’s own reported analysis takes precedence. The recalculation is descriptive and should not be substituted for the reported result.

What is the role of randomization and masking?

In general, random allocation is intended to make treatment groups comparable at assignment, including with respect to factors not measured in the study. Masking is intended to reduce the influence of knowledge of assigned treatment on care, reporting, or assessment. These design features support a fair comparison, but they do not guarantee that groups remain comparable in every respect after allocation. The registry identifies the study as randomized and quadruple-masked; it does not describe the exact allocation procedure or the roles included in that masking label.

Why do unadjusted comparisons need caution?

Multiplicity arises when many outcomes, arms, or comparisons are tested. Even when each test uses a conventional significance threshold, a larger family of tests creates more opportunities for chance findings. Adjustment procedures can address this, but they may affect the interpretation of individual p-values and confidence intervals. The registry record does not report whether or how the primary and secondary comparisons were adjusted for multiplicity. The posted recalculated p-values are unadjusted, so they should not be treated as if they account for all comparisons in the trial.

In general, over-dispersion means that variability in the data is greater than a statistical model assumes. It can make standard errors too small if the model does not allow for that extra variation. This is a general statistical consideration, not a claim that over-dispersion was present in this trial. The primary outcome is reported as a continuous measure, and the registry does not describe a model or a specific over-dispersion assessment.

What can the sample-size illustrations tell readers?

The planning illustrations use the observed effect and stated assumptions to show how participant requirements change when the target effect is reduced or when a different power target is selected. They are not the trial’s original design calculation. For continuous outcomes, such calculations conventionally depend on assumptions about variability, allocation, significance level, and the target difference. The listed planning assumptions specify a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and detection of a stated fraction of the observed effect. The original trial’s assumptions and justification are not reported in the registry record.

These statistical concepts help distinguish the observed estimates from the model-dependent uncertainty around them. They do not supply missing protocol information, establish that all planned analyses were reported, or turn a statistical comparison into a conclusion about clinical importance.

11. Confidence Intervals and Precision

The primary endpoint estimates are accompanied by standard errors at the arm level and by 95% confidence intervals for the registry-reported contrasts. The placebo comparison intervals are -0.97 to -0.25 for pregabalin 150 mg BID, -0.74 to -0.02 for DS-5565 15 mg QD, and -0.58 to 0.13 for DS-5565 15 mg BID. These ranges convey uncertainty in the estimated mean differences under the sponsor’s reported analyses. They are more informative than a point estimate alone because they show a range of contrasts compatible with the data and analysis.

The intervals differ in where they lie relative to zero. The BID interval includes zero; the other two placebo-comparison intervals do not. This is a statement about the reported statistical estimates, not a declaration that one regimen is clinically important or that another has no effect. The intervals also do not account for any multiplicity adjustment unless the analysis did so; that adjustment is not reported in the registry record.

Precision is not the same as accuracy. A narrow interval can indicate a more precise estimate under a given analysis, but it cannot correct bias from missing data, measurement limitations, or an unsuitable model. The posted arm summaries and registry analyses do not provide all information needed to evaluate those issues. In addition, the simple recalculations yield slightly different estimates and intervals from the sponsor’s reported analyses. The sponsor’s reported results take precedence for interpretation.

Finally, the interval for a group mean difference does not describe the range of outcomes among individual participants. The registry does not report a clinically important difference threshold for ADPS. Therefore, the confidence intervals support discussion of statistical uncertainty, but not a conclusion about whether the observed contrasts would be noticeable or important to participants.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size illustrations translate an observed contrast into planning examples. The figures are participants per arm, not total participants across both arms. They use a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and a target effect equal to the stated fraction of the observed effect. They are planning illustrations based on the observed effect, not the original trial’s design calculation; the trial’s own sample-size justification is not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the stated target effect under the listed assumptions, if that effect and the other assumptions hold. The 90% power column gives the corresponding planning number for a 90% chance. These are prospective design concepts, not probabilities that the completed trial produced a correct result. This is not observed power.

Rows planning for 100%, 75%, or 50% of the observed effect ask what a study might require if the target effect were the full observed estimate or a smaller fraction of it. Smaller target effects are harder to distinguish from random variation, so the illustrations require more participants as the target effect gets smaller. The columns for 80% and 90% power also differ because a higher desired chance of detection generally calls for a larger planned sample.

The illustrations depend on assumptions and are not a replacement for a prespecified design calculation. In particular, the observed effect can be an unstable basis for future planning, and the registry record does not report the trial’s original design assumptions. Read the figures as conditional planning examples for the stated pairwise comparison and not as a retrospective judgment of whether the completed study had adequate power.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -0.610; pooled standard deviation σ = 2.326.
2. n = 2 × (1.96 + 0.842)² × 2.326² / -0.610² = 228.3, rounded up to 229 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 <- -0.61                      # observed difference in means
sigma <- 2.32633181113805                     # 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(2187159)
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 = 229 (80% power), 306 (90% power)
 75% of observed effect: n per arm = 406 (80% power), 544 (90% power)
 50% of observed effect: n per arm = 914 (80% power), 1,223 (90% power)
power.t.test: 229.3 
Simulated power at n = 229 per arm: 0.805 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses for the primary outcome as differences of means for placebo versus each active-control or DS-5565 arm. Those results are distinct from the simple unadjusted recalculations based on the posted arm means, standard errors, and group sizes. The recalculated primary comparisons and sponsor-reported comparisons are flagged as discrepant. In keeping with that distinction, the sponsor’s own analysis takes precedence; the recalculation is useful only as a transparent arithmetic comparison of the posted summaries.

The registry-reported results include 95% confidence intervals and p-values for the listed comparisons. For example, the sponsor-reported DS-5565 15 mg QD comparison with placebo is -0.38, with a 95% confidence interval from -0.74 to -0.02. For DS-5565 15 mg BID, the reported comparison is -0.23, with a 95% confidence interval from -0.58 to 0.13. These are the reported analyses, rather than estimates reconstructed from the rounded arm summaries.

The registry record does not explain the cause of the discrepancies or provide enough detail to reconstruct the full sponsor analysis. Potential differences between summary-based arithmetic and a trial analysis can arise from model specification, adjustment, analysis populations, handling of missing observations, or use of unrounded data; these are general possibilities, not established explanations for this study. The reported analysis should therefore be read as the sponsor’s result, while any recalculated value should not be presented as a correction or replacement.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity is relevant because the registry lists 12 outcome measures and 118 analyses, including multiple arms, endpoints, and comparisons. When many statistical tests are conducted, the chance of observing at least one apparently unusual result by chance can increase. A prespecified hierarchy or adjustment method can help define which comparisons are confirmatory and how error rates are controlled. The registry record does not report whether such a hierarchy or adjustment was planned or used. The recalculated p-values are unadjusted and should be interpreted accordingly.

Missing-data handling is another important part of interpretation. The primary outcome is identified as assessed in the modified intent-to-treat analysis set, but the registry record does not explain the exact definition of that set, the amount or pattern of missing ADPS data, or the method used to handle missing observations. It does not report sensitivity analyses for alternative missing-data assumptions. These omissions make it difficult to assess whether incomplete follow-up could have influenced the estimates.

The registry record also does not provide a full primary statistical analysis plan, the model specification, covariate adjustments, or details about interim analyses. It does not report the original sample-size justification. These are unknowns, not evidence that a particular method was or was not used. Randomization and masking are important design features, but they do not answer these analysis questions.

Analysis denominators vary across the posted endpoint records. That can reflect endpoint-specific availability or analysis rules, but the record does not explain the differences. The primary results should therefore be interpreted for the stated modified intent-to-treat set, and secondary comparisons for their own reported analysis groups. In the absence of further detail, claims about complete follow-up, a particular imputation method, or control of the overall false-positive rate are not warranted.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: suicidal ideation (0.6%), ankle fracture (0.3%), transaminases increased (0.3%), supraventricular tachycardia (0.3%), papilloedema (0.3%).

The safety summary reports serious adverse events among participants at risk in each arm: 6 of 315 for placebo, 5 of 312 for pregabalin 150 mg BID, 7 of 315 for DS-5565 15 mg QD, and 11 of 313 for DS-5565 15 mg BID. It separately reports participants with other, non-serious adverse events: 206 of 315, 299 of 312, 290 of 315, and 242 of 313, respectively. The registry also records 0 deaths in placebo, 0 in the pregabalin arm, 1 in DS-5565 15 mg QD, and 0 in DS-5565 15 mg BID.

These counts describe the posted safety record and should be read with their arm-specific denominators. The listed serious adverse-event terms include suicidal ideation at 0.6%, and ankle fracture, increased transaminases, supraventricular tachycardia, papilloedema, and liver injury at 0.3% each. The record does not provide enough detail in this summary to establish event timing, relatedness to assigned treatment, or comparative risk. Counts alone do not establish causation, and differences in counts should not be interpreted as proof of a treatment effect on safety.

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

The results describe mean changes in participant-reported pain scores during a randomized, masked, parallel-group trial, together with registry-reported contrasts between treatment arms. The primary estimates can show how the observed group averages differed under the sponsor’s analysis. Their confidence intervals communicate statistical uncertainty around those contrasts. These findings are relevant to the specific measure, population, regimens, and follow-up period recorded in the trial.

They do not establish how every participant experienced treatment, whether an individual participant would have a similar outcome, or whether any observed difference would be important in daily life. The registry record does not report a threshold for clinically important ADPS change. Statistical evidence against a zero difference is not a substitute for that threshold, and an interval including zero does not prove that the groups are identical.

The results also do not establish equivalence or noninferiority between DS-5565 and pregabalin. Although pregabalin was included as an active control, the registry record does not state that a formal equivalence or noninferiority question was tested. Nor do these results support conclusions beyond the enrolled study population, treatment schedules, and Week 13 assessment described in the record.

Interpretation is further bounded by missing details about the original statistical plan, missing-data methods, multiplicity, and the reason the simple recalculations differ from the sponsor’s analyses. The sponsor-reported primary analyses take precedence. Secondary results offer context but are not a substitute for a prespecified, multiplicity-aware interpretation. Safety counts describe recorded events; they do not establish that treatment caused them or fully characterize risk.

Thus, the posted information supports a focused reading of arm-level ADPS changes and reported contrasts, with explicit uncertainty. It does not support broad claims about clinical benefit, absence of benefit, comparative superiority across all outcomes, or safety causation.

18. Why This Trial Matters Statistically

This trial illustrates several statistical features that matter in clinical research. First, a randomized, masked, parallel-group comparison can report both within-arm changes and between-arm contrasts, but the two answer different questions. A decline in average score within each group does not by itself show how that group compares with placebo. The contrast is the more direct summary for the stated comparative question.

Second, the record shows why point estimates should be read alongside confidence intervals. The reported intervals convey uncertainty and distinguish estimates that include zero from those that do not, while leaving clinical importance to a separate judgment. Without a reported meaningful-change threshold, statistical significance alone cannot determine practical importance.

Third, the record provides a concrete reason to distinguish sponsor analyses from simple recalculations. Rounded group summaries are not necessarily sufficient to reproduce a trial’s own analysis. When the results differ, the sponsor’s reported analysis takes precedence, and the recalculation should remain clearly labeled as an unadjusted reconstruction rather than treated as a correction.

Finally, many endpoints and comparisons raise questions about multiplicity, while incomplete reporting of analysis plans and missing-data methods limits reproducibility. The trial’s secondary outcomes broaden the measured domains, but they do not all have detailed posted results. Together, these features make careful separation of primary and secondary evidence, reported and recalculated estimates, and statistical and clinical interpretation essential.

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.

Several trial-specific limitations of interpretation follow from the registry record. The primary endpoint is participant-reported and based on daily recollection of worst pain over the previous 24 hours, averaged across 7 days. This is the outcome the trial set out to assess, but the registry does not report a clinically important difference threshold for the scale. The statistical size of a contrast therefore cannot be translated from this record alone into a judgment of practical importance.

The sponsor’s reported primary comparisons differ from simple unadjusted recalculations based on the posted summary values. The registry record does not explain why. The sponsor analysis takes precedence, but the absence of sufficient model detail limits independent reproduction and assessment of the discrepancy. The record also does not report the original sample-size justification, full analysis plan, missing-data methods, sensitivity analyses, interim-analysis plan, or multiplicity procedures.

Although 12 outcome measures and 118 analyses are listed, detailed secondary results are available for only some outcomes. This incomplete outcome reporting makes it difficult to assess the full pattern across the planned assessment domains. The registry also gives endpoint-specific analysis denominators that are not always identical and does not explain all differences.

The safety summary provides counts and selected serious adverse-event terms, but does not by itself establish relatedness, timing, or comparative risk. The registry information supports description of these recorded events, not causal conclusions. These limitations concern what can be established from the posted record; they should not be mistaken for evidence that the trial did or did not use procedures that are not described.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Treatment of Pain Associated With Fibromyalgia — NCT02187159.
• Registry record last updated 2020-11-09; status last verified 2020-11.
• Results first posted 2020-11-09.
• 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

NCT02187159 is a completed randomized, quadruple-masked, parallel-group phase 3 trial sponsored by Daiichi Sankyo. It enrolled 1270 participants with pain associated with fibromyalgia and compared DS-5565 15 mg QD and DS-5565 15 mg BID with placebo; pregabalin 150 mg BID was an active-control arm.

The primary endpoint was change from baseline to Week 13 in weekly average daily pain score, assessed in the modified intent-to-treat analysis set. The registry reports arm means and sponsor-reported between-group analyses. Because the simple recalculations differ from those reported analyses, the sponsor’s analyses take precedence. The record lists multiple secondary outcomes, with detailed results posted for only a subset.

Interpretation is limited by unreported details on the original statistical plan, sample-size justification, missing-data methods, and multiplicity. The posted estimates and safety counts describe the recorded outcomes but do not, by themselves, establish clinical importance or causation.