VANISH for Chronic Low Back Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for VANISH for Chronic Low Back Pain (NCT04236804), a randomized na study. The primary outcome is Assessment of Opioid Use Via Subject Report.

2. Clinical Question

3. Trial Design

The registry describes VANISH as a randomized, parallel-group trial of Flowly (TMC-CP01) for chronic low-back pain. It is marked completed, with enrollment of 20. The record lists the start as 2020-06-17 and primary completion as 2024-01-01. Phase is listed as NA. The sponsor is Ajay Wasan, MD, Msc.

Participants were assigned to TMC-CP01 Intervention or Standard of Care. The intervention arm description specifies daily use of TMC-CP01 for 8 weeks in addition to the participant’s current opioid prescription and tapering guidelines. The standard-care arm description specifies the current opioid prescription and tapering guidelines without the device intervention. The record lists no masking. It does not report whether allocation was concealed, how randomization was generated, or what steps were taken to maintain adherence to the assigned groups.

The primary outcome is listed as an assessment of opioid use by subject report, measured in morphine milligram equivalents. Its timeframe is Week 0, and the description says daily oral opioid dose recorded as morphine equivalents will be collected. The displayed group summaries each include 10 participants. This timing matters for interpretation: Week 0 precedes the stated 8-week intervention period, so the primary posted measure cannot by itself describe a treatment-period difference.

The registry also lists secondary outcomes covering opioid use, opioid cravings, heart-rate variability, physical function, fatigue, pain interference, and pain intensity. The posted summaries include selected secondary measures at Week 4 or across weekly assessments. The record lists 44 outcome measures and 43 secondary outcomes posted. It does not report the full protocol, eligibility details, or the trial’s original statistical design assumptions.

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.

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Assessment of Opioid Use Via Subject Report, measured over Week 0.

The primary endpoint is daily oral opioid dose, expressed as morphine milligram equivalents, collected by subject report. Morphine-equivalent units allow opioid doses to be expressed on a common scale despite differences in opioid products. In general, a continuous dose measure can be summarized by a mean to describe the group’s average reported dose and by a standard deviation to show how dispersed participant values are around that average.

The registry states that the primary endpoint timeframe is Week 0. The posted values are means of 47.5 for TMC-CP01 Intervention and 21.75 for Standard of Care, with standard deviations of 36.53 and 23.19, respectively. The mean difference is 25.75, with a confidence interval from -1.068 to 52.57. These are baseline summaries; they do not quantify change after participants used the intervention.

Opioid dose is relevant to the trial’s stated aim of examining pain management and opioid use. But relevance to an aim does not change the meaning of the timing: a Week 0 comparison can describe the groups at the stated starting point, not whether the intervention altered dose during follow-up. The registry record does not report a primary endpoint at the end of the 8-week intervention period.

7. Results Posted in the Registry

• TMC-CP01 Intervention: mean 47.50 versus 21.75 on control; difference 25.75 (95% CI -1.07 to 52.57), standardized effect d = 0.84; z-test p = 0.060.

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.

Assessment of Opioid Use Via Subject Report

• 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:
  • TMC-CP01 Intervention: mean 47.27 versus 10.75 on control; difference 36.52 (95% CI 13.28 to 59.76), standardized effect d = 1.38; z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for TMC-CP01 Intervention than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Opioid Cravings Using the Craving Index at 8 Weeks

• 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:
  • TMC-CP01 Intervention: mean 0.60 versus 0.83 on control; difference -0.23 (95% CI -5.82 to 5.36), standardized effect d = -0.04; z-test p = 0.936.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TMC-CP01 Intervention and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Physical Function Using PROMIS Physical Function Short Form T-score at 8 Weeks

• 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:
  • TMC-CP01 Intervention: mean 0.07 versus -1.41 on control; difference 1.48 (95% CI -1.70 to 4.66), standardized effect d = 0.41; z-test p = 0.362.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TMC-CP01 Intervention and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary outcomes, including opioid use, opioid cravings, heart-rate variability, physical function, fatigue, pain interference, and pain intensity. The posted summaries cover only some of these measures. They include opioid use at Week 4, craving assessments collected weekly, and physical-function change assessed weekly with change from baseline and Week 8 reported. The record also lists pain and fatigue outcomes, but the presence of an outcome in the registry is not itself a posted result.

Across the available secondary summaries, the estimates do not form a single consistent pattern that can be treated as a confirmatory account of the primary question. In general, different outcomes capture different constructs and timeframes; an opioid-use measure, a craving score, and a physical-function score are not interchangeable indicators. Their estimates should be interpreted in relation to their own measurement scales and assessment times rather than combined into a broad claim about benefit.

The primary outcome is a Week 0 opioid-dose measure, while some secondary measures are assessed later or repeatedly. Those secondary observations may describe follow-up patterns, but they do not turn the primary baseline result into a treatment-period estimate. The registry record lists no reported analyses for the posted secondary comparisons. The displayed comparisons are unadjusted, and the record does not report a prespecified hierarchy or a multiplicity adjustment.

When many outcomes or timepoints are examined, the chance of observing an apparently unusual result by chance can increase. This is the general reason unadjusted secondary results carry less weight as confirmatory evidence, especially when the analysis plan and multiplicity strategy are not reported. They remain informative as descriptive results and may help identify questions for future work, but they should not be treated as a set of independent proofs or as a substitute for a clearly specified primary analysis.

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

• Assessment of Opioid Use Via Subject Report
• Assessment of Opioid Use Via Subject Report
• Flowly (TMC-CP01) Virtual Reality Intervention Feasibility Via Change From Baseline in Heart Rate Variability (HRV) at 8 Weeks
• Change From Baseline in Opioid Cravings Using the Craving Index at 8 Weeks
• Change From Baseline in Physical Function Using PROMIS Physical Function Short Form T-score at 8 Weeks
• Change From Baseline in Fatigue Using PROMIS Fatigue Short Form T-score at 8 Weeks
• Change From Baseline in Pain Interference Using the PROMIS Pain Interference Short Form at 8 Weeks
• Change From Baseline in Pain Intensity Using the PROMIS Pain Intensity Item at 8 Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

The posted continuous outcomes are summarized with means and standard deviations. A mean describes the average value in an arm; a standard deviation describes how much the observations vary around that mean. These summaries are useful for orientation, but they do not show the full distribution. In particular, they do not reveal whether values are symmetric, clustered, or strongly influenced by a few observations.

What does the mean difference represent?

For the primary Week 0 outcome, the mean difference is calculated as the TMC-CP01 mean minus the Standard of Care mean. The estimate is 25.75 morphine milligram equivalents. A positive value means that the reported mean is higher in the intervention arm at this baseline timepoint; it does not mean the intervention increased opioid dose. The comparison is unadjusted, and the registry’s own reported-analysis count is zero. The posted comparison is therefore best read as a descriptive, unadjusted contrast of the arm summaries, not as a documented sponsor analysis of a treatment-period effect.

How should the p-value be read?

The primary unadjusted p-value is 0.06. In general, a p-value describes how compatible the observed data are with a specified null model, assuming that model and the analysis conditions hold. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of a difference. The registry record does not report a prespecified hypothesis-testing plan or the significance threshold used for the primary analysis. A planning illustration elsewhere uses a two-sided significance level of 0.05, but that is not evidence that the trial itself adopted that analysis threshold.

The word unadjusted is important. It means the comparison is not reported as adjusted for baseline covariates or for testing multiple outcomes. The record does not report whether the original analysis used a model, whether it included baseline dose, or whether any additional adjustment was planned. It is therefore not possible to treat the displayed p-value as a covariate-adjusted or multiplicity-controlled result.

What does a confidence interval add?

A confidence interval gives a range of values compatible with the data under the method used to calculate it. It conveys uncertainty around an estimate and is usually more informative than a p-value alone. The primary interval, from -1.068 to 52.57, crosses zero. That means the posted data do not sharply distinguish a positive mean difference from no difference or a small difference in the opposite direction. The interval is wide enough that considerable uncertainty remains about the magnitude of the baseline contrast. It is not a range in which individual participants’ doses fall, and it does not account for every possible source of design or measurement bias.

The comparison includes a standardized effect estimate of 0.842. In general, a standardized effect expresses a mean contrast relative to a pooled measure of variability, which can help describe magnitude on a scale less tied to the original units. Its interpretation still depends on the outcome distribution, study design, and uncertainty. It does not turn a baseline contrast into a treatment effect. The record does not report that this standardized effect was part of the trial’s original analysis plan.

Why does variability matter?

The primary standard deviations are 36.53 and 23.19. In general, greater variability makes it harder to estimate a group mean or mean difference precisely, because observations are spread over a wider range. If outcome values have a strongly skewed distribution or influential extremes, a mean and standard deviation may not fully describe what is typical. The registry record does not report distributional checks, robust methods, transformations, or a prespecified alternative summary. The posted summaries alone cannot establish whether the assumptions of a particular inferential method were met.

Over-dispersion is a general concern when observed variability is greater than a model expects. In a continuous outcome, excess variability can lead to uncertainty estimates that are too small if the model does not accommodate it. In a count outcome, it can similarly make a simple count model underestimate uncertainty. The primary endpoint is a continuous dose measure, but the record does not report a model or an assessment of over-dispersion. The posted standard deviations show variation, not whether a model assumption was violated.

What is not documented?

The registry record does not report the randomization sequence method, allocation concealment, protocol-level analysis plan, handling of missing observations, or the population used for analysis. It does not report interim analyses, a sample-size justification for the trial, covariate adjustment, or a method for repeated observations. These omissions do not prove that such procedures were absent; they mean they are not reported in the registry record. Interpretation should remain within the limits of the information recorded.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of 25.75 morphine milligram equivalents, with a confidence interval from -1.068 to 52.57. The interval is wide in relation to the point estimate and includes zero. Thus the estimate is uncertain: values compatible with the data range from a small negative difference to a substantially positive one. The point estimate alone should not be read as a precise measure of the baseline contrast.

A confidence interval is not a guarantee that the true value lies within its endpoints, nor does it describe the spread of individual doses. In general, it summarizes uncertainty for an estimated quantity under the statistical method used. Its width depends on factors including variability, the number of observations, and the analysis method. The posted arm summaries show standard deviations of 36.53 and 23.19, alongside 10 participants in each arm. These features help explain why the estimate should be read cautiously, but the registry record does not report the interval-calculation method or its assumptions.

The unadjusted p-value of 0.06 is consistent with an interval that crosses zero under a conventional two-sided comparison, but the p-value and interval answer different questions: one gives a measure of compatibility with a null model, while the other communicates a range of estimates. Neither provides a direct measure of clinical relevance. Also, because the endpoint is at Week 0, even a more precise interval would describe the baseline difference, not the effect of TMC-CP01 during follow-up.

Precision is limited further by missing documentation about missing observations, outcome distributions, and any planned adjustment. The posted result gives a useful description of the estimated contrast and its uncertainty, but not a complete account of how the trial analyzed its primary outcome.

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 planning values are participants per arm for 80% power and participants per arm for 90% power. They are not total events: the endpoint is continuous, and the listed planning figures are arm-specific participant counts. The planning assumptions stated in the registry record are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The trial’s own original design assumptions are not reported in the registry record.

In plain language, 80% power describes the probability that a study would meet its specified statistical criterion if the assumed effect were the true effect and the planning model were appropriate. The 90% column uses a higher target probability of detecting that assumed effect. These are design targets, not guarantees that a study will detect an effect, and they do not say what happened in this completed trial.

Rows based on 100% of the observed effect use the full observed estimate as a planning target. Rows based on 75% or 50% use smaller effects. Smaller effects are harder to distinguish from random variation, so the planning calculations call for more participants per arm to reach the same power target. This relationship is a general feature of statistical planning, not evidence that the smaller effect is more or less plausible.

These figures are planning illustrations computed from the observed effect, not observed power. They should not be treated as the trial’s original sample-size justification or as evidence about the trial’s probability of finding a result. Because the observed effect can be unstable, particularly in a small trial, planning directly from it can yield highly variable estimates of future sample requirements.

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 = 25.750; pooled standard deviation σ = 30.596.
2. n = 2 × (1.96 + 0.842)² × 30.596² / 25.750² = 22.2, rounded up to 23 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 <- 25.75                      # observed difference in means
sigma <- 30.5958902468943                     # 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(4236804)
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 = 23 (80% power), 30 (90% power)
 75% of observed effect: n per arm = 40 (80% power), 53 (90% power)
 50% of observed effect: n per arm = 89 (80% power), 119 (90% power)
power.t.test: 23.2 
Simulated power at n = 23 per arm: 0.798 (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 lists a primary outcome and numerous secondary outcomes, including repeated or multiple-timepoint assessments. It does not report how the trial addressed multiplicity, such as whether it controlled the overall error rate, used a hierarchical testing sequence, or treated secondary outcomes as exploratory. Because the posted secondary comparisons are unadjusted, their p-values should be read as individual comparisons rather than as results protected against the full set of outcome and timepoint evaluations.

Multiplicity matters because repeated statistical testing creates more opportunities for a result to look unusual by chance. The amount of concern depends on which outcomes were prespecified, which analyses were actually conducted, and how their results were interpreted. Those details are not reported in the registry record. The outcome list alone cannot establish which comparisons were planned as confirmatory or whether all planned outcomes were posted.

The record also does not report how missing data were handled. It does not state whether all randomized participants contributed to each endpoint, how incomplete weekly records were treated, or whether any imputation or sensitivity analysis was used. The arm summaries give participant counts for the displayed outcomes, but they do not explain whether those counts represent all assigned participants or a particular analysis population.

Similarly, the registry record does not define an intention-to-treat population, a per-protocol population, or another analysis set. It does not report the treatment of deviations from assigned intervention, discontinuation, or missing outcome assessments. These are important considerations for a randomized trial because excluding participants or handling missing observations differently can affect comparability between arms.

The primary Week 0 outcome is reported as a mean and standard deviation, but no original analysis plan, covariate strategy, interim-analysis plan, or repeated-measures method is reported. This is particularly relevant to secondary outcomes assessed weekly. The registry record does not say whether repeated observations were modeled jointly, analyzed at selected timepoints, or summarized by another prespecified method. The absence of these details limits reconstruction of the planned statistical approach; it does not establish that an approach was not used.

15. 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 0% reporting threshold.

The adverse-event record lists 10 participants at risk in each arm. Serious adverse events affected 0 participants in the TMC-CP01 Intervention arm and 0 in Standard of Care. Other adverse events affected 0 participants in each arm, and deaths were 0 in each arm. No serious adverse-event terms are listed.

These figures describe the events recorded in the registry for the groups and follow-up captured there. A zero count means no affected participants were reported for that category; it does not establish that an intervention has no risk. The group sizes are small, and the registry record does not provide event definitions, monitoring procedures, individual event details, or a safety analysis plan. It also does not report the duration of safety follow-up separately from the intervention schedule.

Safety counts should be interpreted alongside the design and completeness of reporting. The record marks the trial completed, but it does not explain whether all participants completed follow-up or how missing safety information was handled. These counts therefore provide a concise account of posted events, not a comprehensive estimate of the frequency of uncommon harms or a comparison capable of ruling out risk.

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

The registry record describes a completed randomized study of a virtual-reality-enabled pain-management intervention added to current opioid prescription and tapering guidelines, compared with standard care. Its primary posted measure is daily oral opioid dose at Week 0. The observed mean was higher in the TMC-CP01 arm than in the standard-care arm at that starting-point assessment, and the uncertainty interval for the difference includes zero.

That baseline result does not establish whether TMC-CP01 changed opioid dose, pain, function, or any other outcome during the intervention period. The key limitation is the primary endpoint’s timing: Week 0 is before the stated daily intervention for 8 weeks. A baseline contrast, whether large or small, is not a treatment-effect estimate. The later and repeated secondary measures provide additional descriptions, but the registry record does not report a multiplicity strategy or formal secondary analyses.

The posted data also do not establish the clinical importance of any difference. Statistical estimates describe measured outcomes and uncertainty; clinical importance requires interpretation of the outcome scale, relevant thresholds, patient experience, and the study context. The registry record does not report a threshold for meaningful change in opioid dose or the other listed measures. It also does not provide participant-level data or detailed eligibility information that would support a fuller assessment of applicability.

Accordingly, the record supports a cautious description of the trial design, baseline opioid-dose summaries, selected secondary summaries, and reported adverse-event counts. It does not support a claim that the intervention works or does not work. A treatment-period analysis with clearly documented outcome timing, analysis populations, missing-data handling, and multiplicity procedures would be needed to assess the intervention’s effects more directly.

17. Why This Trial Matters Statistically

This trial is statistically instructive because the primary outcome’s timing is central to what the estimate can mean. A randomized design is intended to support comparisons between assigned groups, but a Week 0 measure is a starting-point description rather than a post-intervention outcome. Recognizing that distinction prevents a baseline imbalance from being mistaken for a response to treatment.

The primary mean difference is accompanied by a confidence interval that includes zero and spans a broad range of possible differences. This illustrates why estimates and their uncertainty should be read together. A point estimate can be visually prominent, but its precision and the endpoint’s timing determine what conclusions it can support. The p-value alone cannot answer questions about effect size, clinical importance, or whether a difference emerged during follow-up.

The trial also illustrates the interpretive challenge of multiple outcomes and repeated measurements. Opioid use, cravings, physical function, pain, fatigue, and heart-rate variability address distinct aspects of the intervention’s stated aims. Without a reported hierarchy or multiplicity plan, isolated unadjusted secondary comparisons should be treated cautiously rather than as a collection of confirmatory findings.

Finally, planning values based on observed effects are not the same as the original trial design rationale or observed power. They can illustrate how assumptions about the effect size influence future sample-size requirements, while also showing why planning from an estimate in a small study may be unstable. Together, these features make endpoint timing, precision, planning assumptions, and transparent analysis reporting essential to a sound reading of clinical trial results.

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 specific to this record restrict interpretation. The most consequential is that the primary endpoint is measured at Week 0, while the intervention is described as daily use for 8 weeks. The primary posted comparison therefore does not assess change during or after the intervention. The record does not list a later primary endpoint for opioid use.

The trial enrolled 20 participants, with 10 shown in each primary-outcome arm. Such a small study can provide limited precision, especially when the reported dose values vary substantially. The confidence interval for the primary mean difference is wide and includes zero. The registry record does not report a sample-size justification or the assumptions used in the original design, so the posted planning illustration should not be mistaken for that rationale.

The record does not report detailed eligibility criteria, participant characteristics, randomization procedures, allocation concealment, adherence, or concurrent care beyond the current opioid prescription and tapering guidelines. These omissions make it harder to assess group comparability, treatment implementation, and the applicability of the findings to other settings or patient groups.

Analysis documentation is also limited. The registry does not report missing-data procedures, analysis populations, covariate adjustment, the original statistical plan, or handling of repeated assessments. No sponsor-reported analyses are listed for the posted secondary comparisons. The number of outcome measures and the range of timepoints make it especially important to know which comparisons were prespecified and whether multiplicity was addressed.

Finally, the safety record shows zero affected participants in the listed event categories, but the registry does not provide detailed definitions, follow-up completeness, or event-level descriptions. These limitations do not show that the trial lacked procedures or that unreported events occurred; they identify information not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: VANISH for Chronic Low Back Pain — NCT04236804.
• Registry record last updated 2025-04-11; status last verified 2025-03.
• Results first posted 2025-04-11.
• 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

VANISH for Chronic Low Back Pain is listed as a completed randomized, parallel-group trial with no masking and enrollment of 20. The record describes Flowly (TMC-CP01), used daily for 8 weeks alongside current opioid prescription and tapering guidelines, compared with standard care. The primary outcome is subject-reported daily oral opioid dose in morphine milligram equivalents at Week 0.

The Week 0 mean dose was 47.5 in the intervention arm and 21.75 in standard care. The posted mean difference was 25.75, with a confidence interval from -1.068 to 52.57 and an unadjusted p-value of 0.06. Because the endpoint is at Week 0, these results describe a baseline comparison, not a treatment-period effect.

The record lists a range of secondary outcomes and reports selected summaries, but no secondary analyses are listed as reported analyses. Serious adverse events, other adverse events, and deaths were recorded as 0 in both arms. Details about the original design assumptions, analysis plan, missing data, and multiplicity are not reported in the registry record.