Primary Care Brief Mindfulness Training for Veterans With PTSD: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Primary Care Brief Mindfulness Training for Veterans With PTSD (NCT03352011), a randomized na study. The primary outcome is Number of Participants With Assessment Retention Assessment Retention.

2. Clinical Question

The registry describes a small randomized clinical trial intended to investigate the feasibility of testing brief mindfulness training for veterans with PTSD in primary care. The intervention was designed for patients who might be reluctant to engage in other mental health treatments. The primary question represented by the posted outcome is whether participants completed all assessment time points from enrollment through 24 week follow-up in each study group.

The registry also lists secondary measures of PTSD symptoms, recovery orientation, depressive symptoms, self-compassion, and health responsibility. The posted secondary results cover some, but not all, of those listed measures. They add descriptive context about outcomes at follow-up, but they do not change what the primary endpoint measures: retention in the assessment process.

3. Trial Design

The registry identifies this as a randomized, single-masked, parallel-group study. A total enrollment of 55 is reported. The two groups were Primary Care Brief Mindfulness Training and PTSD Psychoeducational Class; the posted arm counts are 28 and 27, respectively. The registry status is completed. The study start date is 2018-01-02, and primary completion is dated 2020-02-10.

The intervention is behavioral and group-based, as is the psychoeducational comparator. The registry calls the trial a small randomized clinical trial and frames its purpose as investigating feasibility after adapting the intervention with feedback from Veterans Affairs mental health providers and peer support specialists. No specific details about how randomization was generated or concealed are reported in the registry record. The identity of the party or parties masked is also not reported; “single” is the only masking detail recorded.

The primary outcome concerns assessment retention from enrollment through 24 week follow-up. At that endpoint, the posted participant counts are 24 in the mindfulness group and 25 in the psychoeducational group. The registry lists several secondary outcomes, with posted follow-up results for three measures. It does not report a trial phase beyond the phase designation NA, nor does it provide further design details such as the planned recruitment target’s justification, intervention schedule, or follow-up procedures. Those omissions limit how fully the trial’s design and implementation can be reconstructed from the registry record alone.

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 Number of Participants With Assessment Retention Assessment Retention, measured over enrollment to 24 week follow-up.

The primary endpoint is the number of participants who completed all assessment time points from enrollment to 24 week follow-up. It is a measure of assessment retention: it describes whether participants remained available to complete the study’s assessments over the stated period. It is not itself a measure of PTSD symptom improvement, recovery, or treatment response.

Retention is useful in a feasibility study because it indicates whether participants can be followed through the assessment schedule. If many participants do not complete assessments, estimates of clinical outcomes may become less complete and potentially less representative of the enrolled group. The endpoint can therefore inform the practical feasibility of collecting follow-up data in a future study. It does not, by itself, explain why participants did or did not complete assessments, or whether the intervention was acceptable to them; those details are not reported in the registry record.

The posted counts are 24 participants in the mindfulness group and 25 in the psychoeducational group. The registry characterizes the endpoint as the rate of participants who complete all assessment time points, while reporting a count of participants for each arm. The comparison between those groups is consequently about observed assessment completion, not a direct estimate of the effect of mindfulness training on PTSD symptoms. The definition also matters: completion of all time points is stricter than attendance at a single follow-up assessment. The registry does not provide a breakdown of completion at intermediate time points or reasons for noncompletion.

7. Results Posted in the Registry

• PTSD Psychoeducational Class: 92.6% (25/27) versus 85.7% (24/28) on control; risk difference 6.9 percentage points (95% CI -9.4 to 23.2), risk ratio 1.08 (0.90–1.30); unadjusted two-proportion z-test p = 0.413.

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.

Post-traumatic Stress Checklist for DSM-5

• 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:
  • PTSD Psychoeducational Class: mean 40.89 versus 32.99 on control; difference 7.90 (95% CI -1.19 to 16.99), standardized effect d = 0.49; z-test p = 0.089.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PTSD Psychoeducational Class and the control. The interval gives the range of effects that remain compatible with the data.

Recovery Orientation Scale- 24

• 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:
  • PTSD Psychoeducational Class: mean 82.35 versus 89.53 on control; difference -7.18 (95% CI -15.19 to 0.83), standardized effect d = -0.50; z-test p = 0.079.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PTSD Psychoeducational Class and the control. The interval gives the range of effects that remain compatible with the data.

Patient Health Questionnaire-9,

• 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:
  • PTSD Psychoeducational Class: mean 12.98 versus 9.12 on control; difference 3.86 (95% CI 0.51 to 7.21), standardized effect d = 0.64; z-test p = 0.024.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for PTSD Psychoeducational Class than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the secondary outcomes with posted results, the group means point in different directions depending on the measure. The uncertainty intervals are also not uniform: two of the three reported comparisons span zero, while the Patient Health Questionnaire-9 comparison has an interval above zero. This varied pattern does not form a consistent set of changes across all measured domains, and the measures capture different constructs rather than interchangeable versions of one outcome.

These results complement but do not replace the primary retention outcome. The primary result concerns completion of assessments, whereas the secondary scores describe outcomes among participants with posted follow-up measurements. A difference in a follow-up score cannot explain the observed retention counts, and retention itself does not establish a difference in symptoms or recovery. The registry does not report how participants with missing follow-up scores were handled, so the means should be interpreted as summaries of the observations available for each measure.

The registry lists additional secondary outcomes, including Self Compassion Scale- Short Form and the Health Promoting Lifestyle Profile II: Health Responsibility Subscale, but does not post results for them in the outcome set described. Across the outcomes that are posted, no reported analyses accompany the secondary measures. The comparisons are unadjusted, and the record does not state whether outcomes or analysis choices were prespecified.

When several outcomes are examined, some may appear more compelling than others by chance alone. In general, multiplicity adjustment or a clearly stated hierarchy can help control the interpretation of a collection of tests. Neither a multiplicity strategy nor a hierarchy of secondary outcomes is reported in the registry record. Consequently, isolated unadjusted results carry less weight than a prespecified, fully reported analysis, particularly when several domains are assessed. The secondary results are best treated as exploratory descriptions that may help motivate further study, not as a definitive pattern of effects.

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

• Post-traumatic Stress Checklist for DSM-5
• Recovery Orientation Scale- 24
• Patient Health Questionnaire-9,
• Self Compassion Scale- Short Form
• Health Promoting Lifestyle Profile II: Health Responsibility Subscale

9. Statistical Interpretation

10. Statistical Methods Explained

In general, a randomized parallel-group trial assigns participants to one of two or more groups and compares outcomes between those groups. Randomization can help balance factors that affect outcomes, but it does not guarantee balance in a small study. The registry identifies this trial as randomized and parallel-group, but details of sequence generation, allocation concealment, and any balancing procedures are not reported in the registry record. The record specifies single masking without identifying who was masked.

The primary outcome is a count of participants completing all assessment time points. A risk or proportion summarizes the number with the outcome relative to the number at risk. A risk difference expresses the contrast between two such proportions on an absolute scale. Here, the comparison is reported as the psychoeducational group relative to the mindfulness group. A positive estimate therefore points toward a higher observed completion proportion in the psychoeducational group under that stated ordering; the uncertainty interval is needed to judge how precisely that direction and magnitude are estimated.

The interval for the primary risk difference extends from -0.094 to 0.232. In general, a confidence interval describes a range of values compatible with the data under the statistical procedure used. Its width conveys precision: a broad interval indicates that the estimate is uncertain over a comparatively wide range. An interval spanning zero for a difference means the data do not clearly distinguish a positive difference from a negative difference or no difference. The confidence level used for the posted intervals is not reported in the registry record, so it should not be inferred from the interval values alone.

The p-value for the primary comparison is 0.413. In general, a p-value measures how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the test assumptions held. It is not the probability that the null hypothesis is true, and it is not a measure of clinical importance. A p-value that does not meet a chosen threshold does not prove that the groups are the same. The registry does not report its prespecified significance threshold or a sponsor-reported primary analysis; the posted comparison is an unadjusted comparison based on the arm-level outcome summaries.

The secondary outcomes are continuous scores, reported as group means with standard errors. A mean is the arithmetic average of observed scores. A standard error describes the estimated sampling variability of a mean; it is not the same quantity as the spread of individual participant scores. The registry reports the standard errors for each arm and presents mean differences between groups. It also gives pooled standard deviations and standardized effect estimates for some comparisons. In general, standardization expresses a mean difference in units of a pooled measure of score variability, which can help compare effects measured on different scales. These standardized values are not required to interpret the raw score differences and should not be confused with adjusted analyses.

The registry’s secondary comparison entries are unadjusted. In general, an unadjusted comparison contrasts the groups without accounting for other variables or for a set of multiple outcome tests. The record does not report covariate-adjusted models, a repeated-measures approach, or the method used to handle possible differences in baseline scores. It also does not report outcome-specific analysis populations beyond the arm counts associated with the posted scores.

Over-dispersion is a general concern for count outcomes when variability exceeds that expected under a simple count model. It can make standard errors too small if the model assumes less variability than the data contain. The primary endpoint is reported as a count of participants completing assessments, with a two-arm risk-difference comparison rather than a model for a repeated or highly variable event count. The registry does not describe a count model or report a dispersion parameter, so over-dispersion cannot be assessed from the posted primary result.

None of the secondary outcomes has a reported analysis entry in the registry record. That absence does not mean no analyses were conducted; it means methods such as model specification, handling of missing observations, and any adjustment for multiple testing are not documented in the registry results. The distinction matters because the posted means and unadjusted comparisons are interpretable as descriptive group summaries, but the record does not establish whether they were prespecified, adjusted, or selected from a larger set of analyses.

Finally, a nonsignificant result should not be interpreted as proof of no effect, and a statistically significant result should not be treated as proof of a causal or clinically important effect. Statistical inference depends on the design, assumptions, measurement quality, amount of missing data, and analysis plan. The registry supplies limited detail on these aspects. The estimates and intervals are therefore best read as summaries of the posted data, with the uncertainty and reporting limitations kept in view.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.069, with an interval from -0.094 to 0.232. This interval is broad and crosses zero. It therefore includes values corresponding to a lower completion proportion in the psychoeducational group, little or no difference, and a higher completion proportion. The data do not pin down the direction or size of the difference precisely. The confidence level associated with the interval is not reported in the registry record.

Precision is limited by the number of participants contributing to the primary outcome: 24 in the mindfulness group and 25 in the psychoeducational group, against arm enrollment counts of 28 and 27. The interval is more informative than the p-value alone because it shows the range of contrasts compatible with the analysis, rather than only whether the test crossed a particular threshold. The p-value of 0.413 does not establish equivalence or rule out a meaningful difference.

For the secondary measures, the intervals also show varying degrees of uncertainty. The Post-traumatic Stress Checklist for DSM-5 interval ranges from -1.192 to 16.99, and the Recovery Orientation Scale- 24 interval ranges from -15.19 to 0.831; both span zero. The Patient Health Questionnaire-9 comparison has an interval entirely above zero, but its lower endpoint is close to zero. These intervals concern unadjusted comparisons, and the registry does not report a confidence level or a multiplicity adjustment. They should be interpreted as uncertainty around the individual posted comparisons, not as guarantees that the true effect lies within a particular range.

In general, wider intervals indicate less precision, while narrower intervals indicate more precision, subject to the validity of the model and data. The modest number of observations at follow-up means the estimates may be sensitive to individual observations. The registry does not report sensitivity analyses or alternative model results that would show how robust the estimates are to analytic choices.

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 describe hypothetical future sample sizes under stated assumptions; they are not the number of participants enrolled in this trial. For these non-time-to-event outcomes, the entries are participants per arm, not total events. They are presented for detecting the full observed effect and smaller fractions of that effect. The figures use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect is the stated fraction of the observed effect. The original design assumptions for this trial are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm under which a future study would have an 80% chance of detecting the assumed effect, if the planning assumptions and effect are correct. The 90% power column uses a higher target chance of detecting that same assumed effect and therefore generally requires more participants per arm. These are planning illustrations based on the observed effect, not observed power.

The entries become larger when planning for 75% or 50% of the observed effect rather than the full observed effect. This reflects a general statistical principle: smaller effects are harder to distinguish from random variation, so a study generally needs more participants to detect them at the same target power and significance level. The estimated requirements also depend on the chosen outcome and its observed variability; the planning entries differ across the primary and secondary comparisons. Because the observed effects come from a small trial, they are uncertain estimates and should not be treated as reliable forecasts of the effect in a future study.

The planning figures do not account for any assumptions beyond those stated, such as attrition or additional design features. Those assumptions, and the basis for the original trial’s enrollment target, are not reported in the registry record. The figures are therefore useful as conditional illustrations of how sample-size needs change with the assumed effect, rather than as a reconstruction of the trial’s original design process.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.857; treatment proportion p₁ = 0.926; average p̄ = 0.892.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4398 = 0.8619.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4371 = 0.3679.
4. n = (0.8619 + 0.3679)² / (0.0688)² = 319.7, rounded up to 320 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.857142857142857                          # control proportion
p1 <- 0.925925925925926                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3352011)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 320 (80% power), 428 (90% power)
 75% of observed effect: n per arm = 609 (80% power), 815 (90% power)
 50% of observed effect: n per arm = 1,458 (80% power), 1,951 (90% power)
power.prop.test: 319.7 
Simulated power at n = 320 per arm: 0.807 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity strategy for the secondary outcomes. Multiple outcomes create multiple opportunities to observe a result that appears unusual by chance. In general, researchers can address this issue by prespecifying a primary outcome hierarchy, adjusting the analysis threshold, or clearly identifying secondary analyses as exploratory. Without such information, the unadjusted secondary p-values should not be read as if they were the sole planned test.

The record reports results for three secondary measures, while its listed secondary outcomes include additional measures. It does not explain why results for every listed measure are not posted, whether outcomes were omitted from analysis, or whether results were collected but not entered in the registry. This incomplete reporting makes it difficult to assess the full set of analyses and the possibility of selective emphasis.

Handling of missing data is not reported in the registry record. The primary endpoint counts completion of all assessment time points, but the record does not give reasons for noncompletion, intermediate assessment counts, or a method for handling missing scores on secondary measures. It also does not identify whether analyses used all randomized participants, only participants with available outcomes, or another analysis population. The distinction matters because results based only on participants with observed follow-up data can differ from results that account for missing observations under explicit assumptions.

The registry does not describe imputation, sensitivity analyses, or a missing-data model. It likewise does not report a prespecified statistical analysis plan, covariate adjustments, or whether the analyses followed an intention-to-treat principle. These omissions do not demonstrate that any particular method was used or that missingness biased the results. They mean that the impact of missing data and the robustness of the reported comparisons cannot be determined from the registry record.

In a small study, even a limited number of missing observations can affect the apparent balance and precision of outcome comparisons. The posted follow-up arm counts and outcome-specific counts should therefore be understood as the observations reported for each endpoint, not as proof that every randomized participant contributed to every analysis.

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 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: er visit or hospitalization unrelated to study interventions (16.0%).

The registry reports serious adverse events among 3 of 27 participants at risk in the Primary Care Brief Mindfulness Training group and 4 of 25 participants at risk in the PTSD Psychoeducational Class group. No deaths are reported in either group. For other adverse events, the registry reports 0 affected participants among 27 at risk in the mindfulness group and 0 among 25 at risk in the psychoeducational group.

These are descriptive counts. The at-risk denominators differ from the arm enrollment counts reported for the primary outcome, and the registry does not explain the difference. A comparison based on these counts alone does not establish that the groups have the same or different safety profile; the number of participants is limited, and the record does not give a formal safety analysis or uncertainty intervals.

The registry lists “ER visit or hospitalization unrelated to study interventions” as a serious-event term and reports 16.0%. The record identifies the term as unrelated to study interventions. It does not provide further context in the posted summary that would support a broader causal interpretation. Serious adverse event counts should be read as events reported during the study, not as evidence that an intervention caused them.

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

The primary result answers a narrow question: how many participants completed all assessment time points through 24 week follow-up in each group? The posted counts are 24 of 28 in the mindfulness group and 25 of 27 in the psychoeducational group. The unadjusted comparison has substantial uncertainty, with an interval spanning zero and p = 0.413. This does not establish that the groups are equivalent, nor does it demonstrate a clear difference in assessment retention.

The result does not directly answer whether brief mindfulness training changes PTSD symptoms, recovery orientation, depressive symptoms, or other health outcomes. Those questions relate to the secondary measures, which have posted follow-up summaries for three outcomes. Their analyses are unadjusted, and the registry does not report a multiplicity plan or full analysis methods. They therefore require cautious interpretation, especially when considering a collection of outcomes rather than any one comparison in isolation.

The study is described as a feasibility investigation following adaptation of an intervention with provider and peer support specialist feedback. Its posted findings can inform understanding of assessment completion and provide preliminary outcome summaries in this enrolled group. They do not establish the effectiveness of either group intervention, determine which approach should be used, or show whether results would generalize to other veterans, care settings, or populations. Further design and implementation details needed to judge generalizability are not reported in the registry record.

Statistical significance is not the same as practical importance, and the absence of a statistically significant comparison is not evidence of no effect. The estimates should be considered together with their uncertainty, the modest number of participants, the unreported handling of missing data, and the absence of a detailed analysis plan. The registry’s own description emphasizes feasibility; the posted data should be understood in that context rather than as a conclusive treatment comparison.

17. Why This Trial Matters Statistically

This trial illustrates why the endpoint and the study’s purpose need to be distinguished. Assessment retention is relevant to whether a study can collect follow-up data, but it is not a clinical outcome. A retention comparison may inform feasibility while leaving questions about symptoms or functioning to separate outcome measures. Interpreting the primary result as if it directly measured clinical benefit would conflate these different questions.

The randomized design provides a structured comparison between two group-based behavioral interventions, but the modest enrollment means that the estimates remain imprecise. The primary interval spans differences in both directions, demonstrating why a single p-value cannot communicate the full uncertainty. Reporting the arm counts and interval helps readers see the scale of the evidence and avoid treating a nonsignificant finding as proof of equality.

The secondary results also show the importance of transparent analysis reporting. The outcomes address several distinct domains, but no secondary analysis entries, multiplicity approach, missing-data method, or analysis population are reported in the registry record. Without these details, the secondary findings have less interpretive weight and it is difficult to assess whether the posted results represent a prespecified set of questions.

Finally, the planning illustrations demonstrate a general relationship between effect assumptions and sample size: smaller assumed effects require more participants for the same target power. Such illustrations can support future planning, but the observed effects in a small study are uncertain and are not a substitute for documented design assumptions. The registry does not report the original basis for the enrollment target. These statistical distinctions help keep feasibility evidence, outcome estimates, and future study planning separate.

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 trial-specific limitations restrict what can be concluded from the registry record. Enrollment was 55, and the posted arm counts were 28 and 27. The number contributing to the primary assessment-retention outcome was smaller than the enrollment count in each arm. The registry does not explain why participants were not counted as completing all assessments, or report their reasons for leaving or missing assessments.

The outcome definition requires completion of all assessment time points through 24 week follow-up. The record does not give completion counts at each time point, making it impossible to identify when assessments were missed. It also does not report whether participants who missed an assessment differed from those who completed the study assessments. For the secondary measures, follow-up counts are reported, but missing-data handling is not described.

The registry does not identify who was masked, detail the randomization procedure, or report allocation concealment. It does not give further information about intervention dose, session schedule, adherence, or comparator delivery. These details could affect interpretation of feasibility and the transferability of the findings, but cannot be reconstructed from the record.

Analysis reporting is also limited. The registry does not report the trial’s original sample-size assumptions, a statistical analysis plan, a multiplicity strategy, or a defined analysis population. The secondary comparisons are unadjusted and no analysis entries are reported for those outcomes. The at-risk counts in the safety summary differ from the enrollment counts, and the reason is not stated. These gaps do not establish that methods were inappropriate; they constrain independent assessment of how the reported estimates were produced and how robust they may be.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Primary Care Brief Mindfulness Training for Veterans With PTSD — NCT03352011.
• Registry record last updated 2022-12-22; status last verified 2022-11.
• Results first posted 2022-12-22.
• 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

NCT03352011 is a completed randomized, single-masked, parallel-group study sponsored by Syracuse VA Medical Center. It enrolled 55 veterans with PTSD in primary care and compared group-based Primary Care Brief Mindfulness Training with a group-based PTSD Psychoeducational Class. The primary outcome was completion of all assessment time points from enrollment through 24 week follow-up.

The primary counts were 24 of 28 in the mindfulness group and 25 of 27 in the psychoeducational group. The unadjusted risk-difference estimate was 0.069, with an interval from -0.094 to 0.232 and p = 0.413. Three secondary outcomes have posted follow-up comparisons; their analyses are unadjusted, and the registry does not report multiplicity or missing-data methods. The record frames the study as a feasibility investigation, while detailed original design assumptions and analysis methods are not reported.