BEdtime Sublingual TNX-102 SL as Fibromyalgia Intervention Therapy (BESTFIT): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for BEdtime Sublingual TNX-102 SL as Fibromyalgia Intervention Therapy (BESTFIT) (NCT01903265), a randomized phase 2, phase 3 study. The primary outcome is Mean Change From Baseline in Weekly Average of Daily Pain Scores at Week 12.

2. Clinical Question

The BESTFIT study asked whether TNX-102 SL 2.8 mg, taken sublingually at bedtime, changed pain scores over 12 weeks compared with placebo in patients with fibromyalgia. The primary outcome was the change from baseline in weekly average daily pain scores at Week 12. The registry record also lists sleep disturbance, patient global impression of change, and fibromyalgia impact among the secondary outcomes.

The scale ran from 0 to 10, with higher scores representing worse pain. Thus, a more negative change represents a greater reduction in reported pain scores. The posted estimate is the between-arm mean difference, rather than a direct measure of how any individual participant felt. The registry record describes the study as randomized, double-blind, multicenter, and placebo-controlled. It records an enrollment of 205.

3. Trial Design

The registry record describes BESTFIT as a randomized, double-blind, multicenter, placebo-controlled, parallel-group study. Its official title calls it a Phase 2b study; the phase classification in the record lists Phase 2 and Phase 3. The study status is completed. The record lists the start as 2013-09 and primary completion as 2014-07.

Participants were assigned to TNX-102 SL 2.8 mg tablets or placebo, with one sublingual tablet taken at bedtime each day for 12 weeks. The registry lists 205 participants enrolled. For the primary outcome, the reported intention-to-treat population comprised all randomized patients, with 103 in the TNX-102 SL arm and 102 in the placebo arm. The adverse-event figures use different at-risk counts: 103 for TNX-102 SL and 101 for placebo.

The study was intended to assess safety and efficacy of the bedtime formulation in patients with fibromyalgia. The registry describes TNX-102 capsules, formerly known as very low dose cyclobenzaprine, as an earlier formulation, and states that the trial assessed TNX-102 SL tablets. That background does not establish a treatment effect in this trial.

The registry reports quadruple masking, but does not specify which groups of people were masked. The full protocol, details of the randomization procedure, the original statistical analysis plan, and the trial's sample-size justification are not reported in the registry record. The registry also does not report whether interim analyses were planned or conducted. These omissions limit what can be inferred about design choices beyond the listed trial characteristics and posted outcomes.

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: Screening for eligibility and washout of restricted medications.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Patients in the Intention-to-treat (ITT) population: all randomized patients

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 Mean Change From Baseline in Weekly Average of Daily Pain Scores at Week 12, measured over Baseline, Week 12.

The primary endpoint was mean change from baseline in the weekly average of daily pain scores at Week 12. Participants reported pain using a daily telephone diary and an interactive voice response system. Each daily assessment used a 24-hour recall and an 11-point numerical rating scale, from 0 to 10, with higher scores indicating worse pain. The endpoint therefore summarizes reported pain across time rather than relying on a single day's rating.

Change from baseline is used to describe how scores at follow-up differ from participants' starting scores. Comparing the average change between randomized groups helps distinguish the pattern in the TNX-102 SL arm from change also observed in the placebo arm. The posted values are least-squares means, accompanied by standard errors. The registry identifies the analysis population as the intention-to-treat population, defined there as all randomized patients.

The registry states that “jump to control” was used to replace missing data in each treatment arm. This is relevant because the endpoint depends on repeated diary assessments and missing observations can affect estimated changes. The record does not provide further details about how that method was implemented, the amount of missing data, or sensitivity analyses. The endpoint is a group-level statistical measure; by itself, it does not describe each participant's experience or establish the clinical importance of a difference.

7. Results Posted in the Registry

• TNX-102 SL 2.8 mg Tablets: mean -1.39 versus -0.95 on control; difference -0.44 (95% CI -1.17 to 0.29), standardized effect d = -0.17; z-test p = 0.235.

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.

30% Responder Analysis of IVRS NRS Pain Assessments at Week 12

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • TNX-102 SL 2.8 mg Tablets: 34.0% (35/103) versus 20.6% (21/102) on control; risk difference 13.4 percentage points (95% CI 1.3 to 25.4), risk ratio 1.65 (1.04–2.63); unadjusted two-proportion z-test p = 0.031.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for TNX-102 SL 2.8 mg Tablets than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline to Week 12 in PROMIS T-score for Sleep Disturbance

• 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:
  • TNX-102 SL 2.8 mg Tablets: mean -8.96 versus -5.13 on control; difference -3.83 (95% CI -6.63 to -1.03), standardized effect d = -0.37; z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for TNX-102 SL 2.8 mg Tablets than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Patient Global Impression of Change (PGIC) Responder Status ("Very Much Improved" or "Much Improved" vs All Other Categories) at Week 12

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • TNX-102 SL 2.8 mg Tablets: 30.1% (31/103) versus 16.7% (17/102) on control; risk difference 13.4 percentage points (95% CI 2.0 to 24.9), risk ratio 1.81 (1.07–3.05); unadjusted two-proportion z-test p = 0.023.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for TNX-102 SL 2.8 mg Tablets than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the posted secondary outcomes, the point estimates generally favor TNX-102 SL: the pain-responder proportion and patient-global-impression responder proportion are higher in that arm, while the sleep-disturbance score has a greater decrease. This broad direction is consistent with the direction of the primary pain-score point estimate. The secondary results therefore add context to the pattern of observed outcomes, but they do not remove the uncertainty in the primary comparison.

These outcomes assess different aspects of the trial question. Pain response classifies participants using a threshold, sleep disturbance is a scale-based change, patient global impression records a participant's overall judgment of change, and the registry also lists FIQ-R total score. The record posts results for three of the listed secondary outcomes but does not post a result for FIQ-R total score. A responder measure and a continuous score can differ in how they summarize participant outcomes, so their estimates should not be treated as interchangeable measures of one underlying quantity.

The registry includes unadjusted comparisons for the posted secondary results but does not report adjusted analyses or a multiplicity plan. When multiple outcomes are tested, the chance of at least one apparently notable result can increase. Consequently, a secondary p-value should be interpreted cautiously and in the context of the full set of outcomes, not as definitive confirmation of a treatment effect. The record does not state which endpoints were designated as key secondary outcomes or describe a testing hierarchy. These results are most appropriately viewed as supportive or exploratory evidence, with their uncertainty and reporting limitations kept in view.

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

• 30% Responder Analysis of IVRS NRS Pain Assessments at Week 12
• Change From Baseline to Week 12 in PROMIS T-score for Sleep Disturbance
• Patient Global Impression of Change (PGIC) Responder Status ("Very Much Improved" or "Much Improved" vs All Other Categories) at Week 12
• Change From Baseline to Week 12 in FIQ-R Total Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: each participant contributes a pain score summarized over time, and the reported outcome is change from baseline. The registry reports least-squares means for the two arms and standard errors for those estimates. A least-squares mean is a model-based estimate of an arm's average outcome; the registry record does not describe the model in enough detail to identify its covariates or other specifications. The reported treatment contrast is the difference between the arm estimates.

What does the mean difference represent?

The estimated mean difference is -0.44 for TNX-102 SL relative to placebo. The direction is interpreted using the scale definition: higher pain ratings mean worse pain, so a more negative change means a greater reduction in reported scores. The mean difference summarizes the contrast between group averages. It does not mean that each participant experienced a change of that size, and it does not describe the distribution of individual responses.

The result is based on the intention-to-treat population, which the registry defines as all randomized patients. Intention-to-treat analysis generally aims to preserve the comparison created by randomization by analyzing participants according to their assigned group. The record does not give further details about analysis-set exclusions, adherence, or how participants with incomplete outcome data were handled beyond stating that jump to control was used to replace missing data in each treatment arm.

What does the confidence interval add?

A confidence interval conveys the uncertainty around an estimated contrast. In general, it describes a range of values compatible with the data and the method's assumptions; it is not a range that contains every participant's outcome. For the primary mean difference, the posted interval extends from -1.167 to 0.287. It includes no difference between arms, so the data do not sharply distinguish the estimated contrast from no difference. The interval also includes differences in both directions, which makes the direction and size of the underlying contrast uncertain.

The standard errors reported beside arm means describe uncertainty in those estimates, not the spread of individual pain scores. The registry's posted comparison also gives a pooled standard deviation and a standardized effect estimate. Such standardized measures express a mean difference relative to outcome variability and can help compare outcomes measured on different scales. They do not replace the original scale or determine whether a difference is clinically important. The registry does not report a clinical-importance threshold for this endpoint.

How should the p-value be read?

The primary comparison has an unadjusted p-value of 0.235. In general, a p-value measures how unusual data at least as discordant with the null model would be if that model and the test assumptions held. It is not the probability that the null model is correct, and it does not quantify the size or importance of a treatment effect. An unadjusted value also does not account for testing multiple outcomes unless a multiplicity procedure is applied; whether that was done is not reported in the registry record.

The sample-size planning illustration uses a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. Those are assumptions for the planning illustration, not evidence about the trial's original design process. The original sample-size assumptions and justification are not reported in the registry record.

What does missing-data handling imply?

The record states that jump to control replaced missing data in each treatment arm. In general, this type of approach uses a control-like assumption for missing outcomes in the active-treatment arm, but the registry does not provide the precise implementation details needed to evaluate the assumption in this trial. It does not report the number or pattern of missing observations, the timing of missingness, or sensitivity analyses under alternative assumptions. Missing-data choices can affect estimates when incomplete observations differ systematically from observed ones.

The registry describes the design as randomized, double-blind, multicenter, and parallel group, and lists quadruple masking. These features describe the design framework, but the record does not detail the randomization sequence, allocation concealment, masking roles, or all analysis procedures. No interim analyses or multiplicity plan are described. Statistical interpretation should therefore be limited to the posted estimates and their stated methods, without assuming unreported protocol details.

11. Confidence Intervals and Precision

The primary mean difference is -0.44, with a 95% confidence interval from -1.167 to 0.287. This interval is the main guide to the precision of the primary comparison. It spans no difference and estimates in either direction. The point estimate favors a larger decrease in pain scores with TNX-102 SL, but the interval makes clear that the exact contrast is uncertain. The interval is not evidence that all values within it are equally likely, and it does not describe the range of individual participants' changes.

The standard errors for the arm-specific least-squares means are 0.253 for TNX-102 SL and 0.271 for placebo. Standard errors characterize uncertainty in estimated means; they should not be confused with the variability among individual pain scores. The registry does not give a confidence interval for either arm-specific mean, but does give the confidence interval for the between-arm contrast.

The interval's width reflects limited precision in the estimated contrast. In general, confidence intervals tend to become narrower with more information and wider when the outcome is variable or data are incomplete. The record reports the ITT group sizes and its missing-data approach, but does not report the amount of missing data or enough methodological detail to assess how those factors affected precision.

The posted interval does not settle whether a difference of a particular size would be important to patients. A threshold for clinical importance is not reported in the registry record. Precision and clinical importance are distinct: an estimate can be statistically uncertain, and even a precise estimate would still need context to assess its practical meaning. The secondary outcomes also have their own uncertainty, and their unadjusted estimates should not be treated as independent confirmation of the primary result.

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. They are illustrations based on the observed effect, rather than a reconstruction of the trial's original design. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The illustration considers detecting 100%, 75%, or 50% of the observed effect. The trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the model assumptions are correct. The 90% power column applies the same idea with a higher target chance of detection. Higher target power generally requires more participants. The figures are conditional on the effect size used; they do not promise that a future study will reach a particular result.

The rows that plan for smaller fractions of the observed effect require more participants per arm than those planning for the full observed effect. This is because a smaller contrast is harder to distinguish from random variation. The posted illustration uses the observed estimate as its starting point, so it should not be read as proof that the observed effect is the true effect or that it will recur. These figures are planning calculations, not observed power for BESTFIT. The original design may have used different assumptions, but those are not reported in the registry record.

The planning illustration is separate from the 205 participants enrolled in the trial and the reported arm counts for the primary analysis. It does not describe how many participants were actually needed to achieve a particular result in this completed study. The sample-size curve can be read in the same conditional way: as a depiction of how the planning requirement changes with the effect size under the stated assumptions, rather than as a prediction of the trial outcome.

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 = -0.440; pooled standard deviation σ = 2.653.
2. n = 2 × (1.96 + 0.842)² × 2.653² / -0.440² = 570.8, rounded up to 571 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 <- -0.44                      # observed difference in means
sigma <- 2.65325131524926                     # 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(1903265)
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 = 571 (80% power), 765 (90% power)
 75% of observed effect: n per arm = 1,015 (80% power), 1,359 (90% power)
 50% of observed effect: n per arm = 2,284 (80% power), 3,057 (90% power)
power.t.test: 571.8 
Simulated power at n = 571 per arm: 0.801 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary outcome and lists secondary outcomes, but does not report a multiplicity adjustment, a testing hierarchy, or the original statistical analysis plan. This matters because examining several outcomes can increase the chance that at least one unadjusted comparison appears statistically notable even when the underlying effects are absent or smaller than estimated. The posted secondary p-values should therefore not be interpreted as if each were the only test in the study. Whether any multiplicity control was prespecified or used is not reported in the registry record.

The primary comparison is reported with an unadjusted p-value, and secondary comparisons are also posted as unadjusted results. No separate adjusted analysis results are reported for the secondary outcomes. The registry record also does not report interim analyses. Without these details, the family of analyses and the decision rules used to interpret them cannot be reconstructed from the posted record alone.

For missing data, the primary endpoint description states that jump to control was used to replace missing data in each treatment arm. The intention-to-treat population is described as all randomized patients. However, the registry does not report how many endpoint observations were missing, when they were missing, or the detailed assumptions and implementation of the replacement method. It also does not post sensitivity analyses that would show how results change under alternative missing-data assumptions.

These gaps do not invalidate the reported estimates, but they constrain their interpretation. The registry record does not provide enough information to assess the robustness of the findings to alternative analysis choices or to establish how fully the reported method matched the prespecified plan. Such plan and implementation details are not reported in the registry record.

15. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cholecystitis (1.0%).

The serious adverse-event figures report 0 affected participants among 103 at risk in the TNX-102 SL arm and 1 among 101 at risk in the placebo arm. These are participant counts, not event rates for every possible adverse event. The registry lists cholecystitis at 1.0% among the top serious adverse-event terms, but does not identify an arm for that term in the posted summary.

The record also reports 65 participants with other adverse events among 103 at risk in the TNX-102 SL arm and 14 among 101 at risk in the placebo arm. The registry's summary does not give further detail about the definition of this category, event severity, timing, or whether participants could contribute more than one event. Death counts are not reported in the registry record.

These figures are descriptive safety data from this trial. The serious-event counts are small, so they provide limited precision for comparing uncommon outcomes. Differences in the listed counts should not be treated as proof of a causal difference between arms. The registry record does not provide enough detail to characterize the full safety profile or determine the clinical significance of individual events.

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

The primary result describes a greater average reduction in pain scores in the TNX-102 SL arm than in the placebo arm, with an estimated mean difference of -0.44. Its confidence interval extends from -1.167 to 0.287, and its unadjusted p-value is 0.235. The interval includes no difference and effects in either direction, so the estimate is not precise enough to establish a clear between-arm difference from the posted data.

This does not mean the two treatments are proven equivalent. A result that does not establish a clear difference can reflect uncertainty, and the confidence interval shows a range of contrasts compatible with the data under the analysis assumptions. Nor does the point estimate alone establish that TNX-102 SL improves outcomes. The trial result should be described as an estimate with uncertainty, not as a definitive conclusion about treatment efficacy.

The secondary outcomes have more favorable point estimates for TNX-102 SL, but their unadjusted status and the absence of a reported multiplicity plan limit the strength of conclusions that can be drawn from them. The record does not report a clinical-importance threshold, longer-term outcomes, or enough detail to evaluate robustness to different missing-data assumptions. The results address the stated 12-week outcomes and should not be extended to effects beyond the measured follow-up.

The findings also do not establish how the result would apply to people outside the trial population or setting. The registry identifies participants with primary fibromyalgia and a multicenter design, but does not give enough participant-characteristic detail in the posted information to assess representativeness. In general, statistical evidence, clinical importance, safety, and applicability are related but distinct questions. The posted results inform the first of these only to the extent permitted by their precision and reporting detail.

17. Why This Trial Matters Statistically

This trial is statistically informative because it reports a randomized, placebo-controlled comparison of a continuous pain measure, along with several secondary outcomes. Randomization provides a design framework for comparing assigned groups, while the placebo arm helps place changes in the active arm in context. The primary result also demonstrates why the direction of a point estimate should not be considered apart from its uncertainty.

The contrast is estimated as -0.44, but the confidence interval includes no difference and extends to estimates in the opposite direction. That combination is a useful example of the distinction between an observed estimate and the strength of evidence about the underlying contrast. The arm-specific changes alone could suggest improvement in both groups; the randomized between-arm comparison is the more relevant estimate for the trial question.

BESTFIT also illustrates how secondary outcomes can provide a coherent-looking pattern without replacing a primary analysis. Several secondary point estimates favor the TNX-102 SL arm, yet the registry does not report a multiplicity strategy or adjusted secondary analyses. That reporting limitation matters when several outcomes are considered together. The record's brief description of missing-data handling is also a reminder that repeated-measure outcomes depend on assumptions about incomplete observations.

Finally, the planning illustration should be kept separate from the trial's observed results and original design. It shows how required participants per arm depend on the effect targeted and the stated assumptions, but does not reveal the trial's own sample-size rationale. Reading these elements together encourages attention to estimate, precision, analysis assumptions, and completeness of reporting rather than relying on a single p-value.

18. Limitations

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

The registry record leaves several details that would help evaluate this trial's methods unreported. It does not give the full statistical analysis plan, original sample-size justification, interim-analysis plans, multiplicity procedures, or a testing hierarchy. It lists quadruple masking but does not identify which groups were masked. The randomization procedure and allocation-concealment details are also not reported.

For the primary endpoint, the record states that jump to control was used for missing data but does not provide the amount or pattern of missingness, detailed implementation, or sensitivity analyses. These omissions make it difficult to assess the dependence of the estimate on missing-data assumptions. The record does not give a threshold for clinical importance, so statistical estimates cannot be translated into a judgment about the practical importance of the observed contrast.

Although four secondary outcomes are listed, the registry posts results for three, and no separate result for FIQ-R total score is reported. The reported secondary comparisons are unadjusted, and no multiplicity adjustment is described. This limits the weight that can be placed on isolated secondary findings. The safety summary gives participant counts but limited information about event timing, severity, definitions, or arm attribution for the listed serious-event term; death counts are not reported in the registry record.

The registry identifies the study as multicenter and reports enrollment, but the posted information does not provide enough detail to assess the full characteristics of participants or how closely they represent other populations. These limitations concern the available reporting and do not by themselves show that the results are biased. They do constrain how fully the methods, robustness, and broader applicability can be assessed.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: BEdtime Sublingual TNX-102 SL as Fibromyalgia Intervention Therapy (BESTFIT) — NCT01903265.
• Registry record last updated 2016-12-23; status last verified 2016-10.
• Results first posted 2016-12-23.
• 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

BESTFIT (NCT01903265) was a completed randomized, double-blind, multicenter, placebo-controlled, parallel-group study of bedtime TNX-102 SL 2.8 mg in patients with primary fibromyalgia. The record lists an enrollment of 205 and a 12-week treatment period. The primary outcome was change from baseline in weekly average daily pain scores at Week 12, measured on an 11-point scale on which higher scores represented worse pain.

The posted primary mean difference was -0.44, with a 95% confidence interval from -1.167 to 0.287 and an unadjusted p-value of 0.235. The estimate favors a greater score reduction with TNX-102 SL, but its interval includes no difference. Secondary point estimates generally favored TNX-102 SL, although the registry does not report a multiplicity plan or adjusted secondary results. The record describes a missing-data method but omits details needed to assess its implementation and robustness.