An Adaptive Walking Intervention to Manage Chronic Pain in Veterans With Opioid Use Disorder Engaged in Opioid Agonist Treatment: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Adaptive Walking Intervention to Manage Chronic Pain in Veterans With Opioid Use Disorder Engaged in Opioid Agonist Treatment (NCT05051644), a randomized phase 1 study. The primary outcome is Retention.

2. Clinical Question

The trial addresses whether a behaviorally focused pain program can be delivered alongside opioid agonist treatment in a population that the registry describes as frequently excluded from pain-treatment studies. Its primary endpoint is treatment retention, measured as the number of attended sessions, with higher numbers indicating better retention. This is an implementation-oriented question: attendance describes whether participants remained engaged with the scheduled treatment, not whether pain or opioid use changed.

The registry also lists pain interference as a secondary outcome. That measure concerns a different aspect of the study: participants’ reported experience of how pain interferes with activity. The results therefore speak to several distinct questions, and the attendance outcome should not be treated as a substitute for a pain outcome. The registry record does not report a primary efficacy question about pain reduction or opioid use.

The main comparison is between S2C and the behavioral control, rather than between treatment and no contact. Both groups were scheduled for weekly sessions over four consecutive weeks. The posted results show similar average attendance, with an unadjusted recalculation of the group difference that is imprecise. The findings describe this trial’s observed outcomes; they do not establish that either program is clinically effective or ineffective.

3. Trial Design

The registry describes a randomized, double-masked, parallel-group phase 1 study with 60 participants. The trial status is completed. The record lists an actual study start of 2022-04-01 and a primary completion date of 2025-02-28. It identifies the VA Office of Research and Development as sponsor and lists chronic pain and opioid use disorder as conditions.

Participants were allocated to Steps 2 Change (S2C) or a behavioral control. The posted group summaries include 30 participants in each group for the primary retention result. S2C sessions were scheduled to last 30-45 minutes and occur weekly over four consecutive weeks in an outpatient opioid agonist treatment clinic. The program included pain education and a pedometer-assisted adaptive walking approach. Participants were expected to increase their average step counts by 10% over the prior week’s average.

The control group was also scheduled for 30-45 minute weekly sessions over four consecutive weeks. Its described focus was problems associated with medication for opioid use disorder, substance use, and general self-management strategies; the description says the group would explicitly avoid pain-coping skills. This comparison helps distinguish the S2C package from a behavioral program with different content, while retaining scheduled treatment contact in both groups.

The registry labels the study double-masked, but which people were masked and how masking was maintained are not reported in the registry record. The original design assumptions, including the planned sample-size rationale, are not reported in the registry record. Nor is a detailed account of allocation procedures or any changes to the design reported. The record describes repeated outcome assessment using a mobile device and study-provided pedometers, but it does not provide further detail about the assessment schedule or the analysis population.

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: After consent and screening visit, participants began 7-days of baseline mobile surveys including three random and one end of day survey per day (4 total). To be randomized, Veterans will need to complete at least 3 end of day surveys with complete step and pain interference data. If a Veteran fails to complete surveys in first 2 days of baseline EMA week, research staff will contact Veteran to assess for technical difficulties and encourage survey completion.

Overall Study

Reasons for not completing this period:

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 Retention, measured over Up to 5 weeks.

The primary endpoint is retention, defined as the number of treatment sessions attended, with values from 0-4 and higher values representing more attendance. The registry gives a timeframe of up to 5 weeks and summarizes the endpoint as a mean with a standard deviation. It is a measure of engagement with the scheduled treatment, not a direct measure of pain intensity, pain interference, opioid use, or clinical improvement.

Attendance is relevant in a feasibility-oriented phase 1 study because an intervention can only be evaluated in practice if participants can attend its sessions. The endpoint can describe whether participants remained involved in the program, and the comparison can show how attendance was distributed between S2C and the control. It does not, by itself, explain why someone attended or did not attend, whether the intervention was acceptable, or whether the content changed participants’ health outcomes. Those interpretations require additional outcomes and supporting information.

The posted group means are 3.7 sessions for S2C and 3.6 for control, with standard deviations of 0.5 and 0.9, respectively. The displayed comparison is an unadjusted recalculation from the posted summary statistics. The registry record does not report a separate sponsor analysis for this primary result or further details about the handling of incomplete attendance records.

7. Results Posted in the Registry

• Steps 2 Change (S2C): mean 3.70 versus 3.60 on control; difference 0.10 (95% CI -0.27 to 0.47), standardized effect d = 0.14; z-test p = 0.595.

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.

Pain Interference

• 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:
  • Steps 2 Change (S2C): mean 0.80 versus 0.90 on control; difference -0.10 (95% CI -1.37 to 1.17), standardized effect d = -0.04; z-test p = 0.877.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Steps 2 Change (S2C) and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome is pain interference, whereas the primary endpoint is session attendance. The outcomes therefore describe different dimensions of the trial: engagement with the scheduled program and the reported impact of pain. Taken together, the record does not present a secondary pattern that clearly changes the interpretation of the primary retention comparison. The secondary results are better viewed as additional descriptive information than as confirmation of an attendance finding.

The registry lists one secondary outcome in the posted results. The recalculated comparison and the registry-reported mean-change analysis are not identical presentations, and the record does not explain their relationship. This limits how confidently the two summaries can be combined. The result table should be consulted for the actual estimates and intervals rather than treating one summary as a definitive explanation of the other.

Unadjusted secondary findings carry less weight when the record does not describe a multiplicity plan. When several outcomes or analyses are examined, the chance of seeing a seemingly notable result by chance can increase. Adjustment methods or a prespecified hierarchy can address this issue, but the registry record does not report whether such methods were planned or used. This does not make the secondary outcome irrelevant; it means that its interpretation should be cautious and should not be treated as a stand-alone confirmatory claim.

In this study, the distinct outcome roles matter as much as the numerical pattern. Attendance can inform whether participants engaged with sessions, while pain interference can describe a symptom-related outcome. Neither alone answers all questions about feasibility, acceptability, or clinical outcomes. The secondary result cannot establish that the intervention changed pain, and it does not turn the primary attendance comparison into a test of pain benefit.

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

• Pain Interference

9. Statistical Interpretation

10. Statistical Methods Explained

The posted continuous outcomes are summarized using means and standard deviations. A mean is the arithmetic average of the observed values, while the standard deviation describes how spread out those values are around the average. These summaries are useful for a broad comparison, but they do not show every participant’s result or the full shape of the outcome distribution.

What does the mean difference represent?

For retention, the comparison is expressed as the S2C mean minus the control mean. The displayed estimate is 0.1 sessions. A positive value means the average is higher in S2C under this direction of subtraction; it does not establish that the intervention caused the difference. The recalculation is unadjusted, meaning it uses the posted group summaries without accounting for other variables. The registry record does not report an adjusted primary analysis or the method used for a sponsor analysis.

The primary group summaries are 3.7 sessions with a standard deviation of 0.5 in S2C, and 3.6 sessions with a standard deviation of 0.9 in control. The comparison also reports a pooled standard deviation of 0.728 and a standardized effect estimate of 0.137. A standardized effect expresses the mean difference relative to the outcome’s variability, which can help describe the scale of a difference. It does not alter the underlying attendance values, and it should not be mistaken for a measure of clinical importance.

How should the confidence interval and p-value be read?

The 95% confidence interval for the recalculated mean difference is -0.268 to 0.468. A confidence interval is a statistical range reflecting the uncertainty around an estimate under the analysis assumptions. If a difference of zero is compatible with the range, the data do not clearly distinguish the observed estimate from no mean difference. The p-value of 0.595 is an unadjusted measure of how unusual the observed result, or a more extreme result, would be under a null model of no group difference. It is not the probability that the null hypothesis is true, nor does it measure the probability that the intervention succeeds.

These calculations are simple unadjusted recalculations from the posted summary statistics. They are not a substitute for a prespecified analysis using participant-level records. The registry record does not report details needed to assess adjustments, model diagnostics, or the treatment of any incomplete observations. The calculation’s interpretation therefore depends on the summary data and assumptions stated for the comparison.

What does standard deviation add?

Standard deviations provide context for the mean difference. For the primary endpoint, the posted standard deviations are 0.5 for S2C and 0.9 for control. These values describe variability within each group, not uncertainty in the mean itself. The standard error is a measure of uncertainty in an estimated mean; the posted standard errors are 0.091 for S2C and 0.164 for control. A confidence interval for a group difference reflects uncertainty in the comparison, rather than simply displaying the range of participant-level observations.

For the secondary pain-interference summary, the group means are 0.8 for S2C and 0.9 for control, with standard deviations of 2.1 and 2.8. The unadjusted recalculated mean difference is -0.1, with a 95% confidence interval from -1.366 to 1.166 and p = 0.877. The reported registry analysis separately gives a mean change of 0.34, with a 95% confidence interval from -0.94 to 1.63, and no p-value. The registry record does not explain how this reported mean-change analysis relates to the simple recalculation, so they should not be collapsed into a single estimate.

Why can over-dispersion matter?

General statistical explanation: when outcome variability is greater than a model assumes, standard errors and confidence intervals can be too small if the model does not account for that extra variability. That can make results appear more precise than they are. The posted outcomes are continuous summaries with standard deviations; the registry record does not report a model-based analysis or an over-dispersion assessment. This general issue should not be taken to mean that over-dispersion was present in this trial.

What is not specified about the analysis?

The registry record does not report the primary analysis plan, the statistical model used by the sponsor, an adjustment strategy, or rules for handling missing observations. It also does not report an interim-analysis plan or a named analysis population. Such omissions limit the ability to establish whether the posted summaries were the only analyses, whether any prespecified decisions were followed, or how the results would change under alternative assumptions. The recalculations are descriptive aids based on the available summaries, not a reconstruction of the full trial analysis.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of 0.1 sessions, with a 95% confidence interval from -0.268 to 0.468. The interval covers zero and values on both sides of zero. In plain terms, the posted summaries do not pin down whether average attendance was somewhat lower or higher in S2C than in control. The interval is more informative than the point estimate alone because it shows the uncertainty around that estimate.

The confidence interval is not a range containing 95% of individual attendance values. It concerns the estimated group difference under the calculation’s assumptions. Nor does it guarantee that the true difference lies inside this particular interval. Its usual interpretation is tied to the repeated-sampling properties of the method, rather than certainty about an individual result.

The secondary pain-interference recalculation also has an interval that includes zero, from -1.366 to 1.166. The separate registry-reported mean-change result has a 95% interval from -0.94 to 1.63. These intervals are broad relative to their respective estimates, so the posted summaries do not tightly locate the group contrast. The record does not explain the relation between the recalculated contrast and the reported mean-change result.

Precision is shaped by the number of observations, variability, and the analysis method. The primary comparison includes 30 participants in each group. The secondary summary includes 30 in S2C and 29 in control. The registry record does not report why the secondary group count differs or how missing data were handled. These limitations matter when interpreting how much weight to put on an estimate, especially when the interval allows more than one plausible direction of effect.

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 table and curve are planning illustrations based on the observed effect, not the trial’s original design calculation. These figures are participants per arm for the continuous outcomes in this record; they are not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if the effect and model assumptions hold. The 90% power column gives the corresponding planning quantity for a 90% chance. These are prospective design quantities, not descriptions of the probability that this completed study found a real effect. This is not observed power.

Rows planning for 100%, 75%, and 50% of the observed effect let readers see how the target effect size changes the required enrollment. The calculations show that smaller effects need more participants to be detected with the same power and assumptions. That pattern is a general property of planning calculations: a subtler signal is harder to distinguish from random variation unless the study has more information.

The table is an illustration rather than a recommendation for a future trial. Its values depend on the observed effect in this study, which is uncertain, and on the stated calculation assumptions. The registry record does not report the trial’s original sample-size justification or its original design assumptions. The curve should be read in the same way as the table: as a depiction of planning requirements across effect assumptions, not as evidence about the actual power achieved or a guarantee of results in another study.

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 = 0.100; pooled standard deviation σ = 0.728.
2. n = 2 × (1.96 + 0.842)² × 0.728² / 0.100² = 832.0, rounded up to 832 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 <- 0.1                      # observed difference in means
sigma <- 0.728010988928052                     # 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(5051644)
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 = 832 (80% power), 1,114 (90% power)
 75% of observed effect: n per arm = 1,480 (80% power), 1,981 (90% power)
 50% of observed effect: n per arm = 3,328 (80% power), 4,456 (90% power)
power.t.test: 832.9 
Simulated power at n = 832 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 does not report a multiplicity strategy for the primary and secondary outcomes or for the three listed analyses. It does not say whether outcomes were arranged in a hierarchy, whether statistical significance was adjusted for multiple comparisons, or whether the secondary analysis was intended to be confirmatory. Without that information, nominal p-values should be interpreted as unadjusted evidence for their specific comparisons, not as accounting for all analyses conducted.

The record identifies five outcome measures but posts one secondary outcome. It does not describe the other outcome measures or explain whether they were collected, analyzed, or omitted from the posted results. The total number of analyses listed is three, but the registry does not identify a broader analysis plan. This creates uncertainty about the full set of comparisons considered and makes it difficult to judge selective reporting or the overall false-positive risk.

The primary retention summaries include 30 participants in each group. The secondary pain-interference summaries include 30 participants in S2C and 29 in control. That difference in posted group counts is visible, but the reason is not reported in the registry record. The record does not specify missing-data definitions, reasons for missing observations, imputation, sensitivity analyses, or whether analyses included all randomized participants. It would be inappropriate to assume that the one-person difference was caused by a particular event or that a particular missing-data method was used.

The registry labels the study randomized and double-masked, but the details of the analysis population and masking procedures are not reported in the registry record. The primary endpoint is an attendance count, but the record does not say how records were verified or how incomplete attendance information was handled. The trial’s own planned statistical analysis and original sample-size assumptions are also not reported. These unknowns constrain assessment of prespecification and robustness; they do not change the numerical summaries posted in the results.

No interim-analysis plan or stopping rule is reported in the registry record. Their absence from the record should not be interpreted as proof that no such procedures existed; it means that the available information does not establish them. A fuller protocol or statistical analysis plan would be needed to evaluate these issues.

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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: drug overdose (6.7%), suicidal ideation (3.3%), shortness of breath (3.3%).

The posted adverse-event figures list serious adverse events affecting 2 of 30 participants in S2C and 4 of 30 in control. The record reports zero deaths in both groups. Other adverse events affected 14 of 30 participants in S2C and 10 of 30 in control. These are counts within the posted group summaries; they do not by themselves establish that the intervention caused or prevented an event.

The serious-event terms listed across the record are Drug Overdose at 6.7%, Suicidal Ideation at 3.3%, and Shortness of breath at 3.3%. The record does not give an arm assignment for each listed term in the information here, so the terms should not be attributed to a particular group. It also does not provide event-level timing, severity detail beyond the serious classification, or an explanation of relatedness to treatment.

Adverse-event summaries in a trial of this size are descriptive. The counts are not precise comparisons of risk and do not establish safety equivalence between groups. Event definitions, ascertainment methods, and follow-up details beyond the posted information are not reported in the registry record. These figures should therefore be read as a summary of what was recorded, rather than as a complete assessment of the safety profile.

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

The posted results describe a randomized comparison of S2C with a behavioral control among Veterans receiving opioid agonist treatment. The primary result is average session attendance. The group means are close, and the unadjusted recalculated difference has an interval that includes zero. The available information therefore does not establish a clear difference in retention between the groups, while also leaving room for differences in either direction.

This finding does not show that the interventions are equivalent. Establishing equivalence would require a defined margin and an analysis designed for that question; neither is reported in the registry record. A non-significant comparison does not prove that there is no meaningful difference. It only indicates that this result, under the stated calculation, does not provide strong evidence against a null difference.

The attendance result also does not establish that S2C reduces pain or improves other health outcomes. Pain interference is posted as a secondary outcome, but it is distinct from the primary attendance measure and is not a substitute for a primary clinical efficacy result. The registry record does not report an outcome on opioid use in the posted results. It would go beyond these data to infer effects on opioid use, pain conditions, or longer-term outcomes.

The study’s stated focus includes feasibility and acceptability, but the registry does not report a formal threshold for deciding whether the intervention was feasible or acceptable. Session attendance is relevant to engagement, yet it cannot alone demonstrate acceptability or explain barriers to participation. The outcome summaries can inform discussion of observed attendance, but they do not supply every component needed to decide whether a program is ready for broader implementation.

Finally, the trial’s setting and participants define the scope of the evidence. It concerns Veterans with chronic pain and opioid use disorder engaged in opioid agonist treatment, with the intervention delivered in an outpatient clinic context. The posted results should not be generalized automatically to people outside that population or to different treatment settings. The record’s missing analysis details further limit conclusions about precision and robustness.

17. Why This Trial Matters Statistically

This trial raises a statistical question that is distinct from the usual efficacy question: can a behavioral pain program be studied alongside opioid agonist treatment in a population often excluded from pain-treatment studies? The registry describes a feasibility- and acceptability-oriented intervention and measures treatment retention as its primary endpoint. That makes careful separation of engagement outcomes from clinical outcomes especially important.

The randomized parallel-group design offers a comparison between two scheduled behavioral programs, rather than a simple contrast between treatment and no contact. This can help readers understand what the observed attendance comparison represents. At the same time, the primary endpoint summarizes only the number of attended sessions. It cannot show which intervention components participants found useful, whether barriers differed, or whether attendance translated into a change in pain interference.

The interval around the primary recalculated estimate illustrates why a point estimate alone is insufficient. The mean difference is small in the posted summary, but the confidence interval extends on both sides of zero. A precise estimate and an inconclusive estimate are not the same thing as proof of no difference. The planning illustrations also show the importance of effect-size assumptions: detecting a smaller effect requires more participants under the stated assumptions.

The record highlights the value of transparent reporting. Details about the original sample-size rationale, missing-data handling, multiplicity, analysis populations, and the relationship between secondary summaries are not reported. Those details would help readers assess how much confidence to place in the results and how to plan later research. The statistical lesson is not to overstate a limited comparison, but to distinguish what was measured, what was estimated, and what remains unresolved.

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 posted primary comparison is a simple unadjusted recalculation from summary statistics, and the registry record does not report a separate sponsor analysis or its method. Summary-level results do not permit independent checks of participant-level distributions, model assumptions, or adjusted estimates. The comparison should therefore be understood as descriptive rather than as a full reanalysis of the trial.

The study enrolled 60 participants, with 30 in each group for the primary result. This is a phase 1 study, and the confidence interval remains compatible with effects in either direction. The original sample-size justification and design assumptions are not reported in the registry record. The planning illustrations use the observed effect and should not be taken as a record of how enrollment was originally chosen.

Only one secondary outcome is posted here, despite the registry identifying five outcome measures. The record does not explain the status of the other measures or identify a complete multiplicity plan. For pain interference, the posted recalculation and the separately reported mean-change analysis are presented without an explanation of their relationship. The secondary group counts also differ, and the reason is not reported.

The registry does not report missing-data methods, analysis populations, the detailed primary statistical plan, masking procedures, or an interim-analysis plan. Nor does the posted attendance summary describe the distribution of attendance or reasons for nonattendance. These limitations leave uncertainty about robustness and the completeness of outcome reporting. They do not establish that the results are biased, but they narrow the conclusions that can be drawn from the registry record alone.

Finally, the trial’s population and setting are specific: Veterans with chronic pain and opioid use disorder engaged in opioid agonist treatment, with sessions scheduled in an outpatient clinic. The registry summaries do not establish how results would translate to other populations, services, or implementation arrangements.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: An Adaptive Walking Intervention to Manage Chronic Pain in Veterans With Opioid Use Disorder Engaged in Opioid Agonist Treatment — NCT05051644.
• Registry record last updated 2026-02-04; status last verified 2026-02.
• Results first posted 2026-02-04.
• 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

This completed, randomized, double-masked, parallel-group phase 1 trial enrolled 60 participants and compared Steps 2 Change with a behavioral control among Veterans with chronic pain and opioid use disorder engaged in opioid agonist treatment. The primary endpoint was treatment retention, measured as the number of sessions attended over up to 5 weeks.

The posted primary group means were 3.7 sessions for S2C and 3.6 for control. The unadjusted recalculated mean difference was 0.1 sessions, with a 95% confidence interval from -0.268 to 0.468 and p = 0.595. Pain interference was posted as a secondary outcome, with both a recalculated comparison and a separate registry-reported mean-change result. The registry also posted serious and other adverse-event counts and zero deaths in both groups.

The record does not report the original sample-size rationale, a detailed analysis plan, missing-data methods, or a multiplicity strategy. The findings describe the posted results and their uncertainty; they do not establish clinical benefit, equivalence, or an effect on outcomes not reported.