Feasibility of Remote Tai Chi: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Feasibility of Remote Tai Chi (NCT05693805), a randomized na study. The primary outcome is Participant Satisfaction Post Treatment With Interventions Being Tested.

2. Clinical Question

The registry identifies the study as randomized, single-masked, and parallel-group. The identity of the masked party is not reported in the registry record. The stated aim was to refine the interventions and assessment procedures, then assess the feasibility and acceptability of a remotely delivered randomized trial. The registry record does not establish that the posted satisfaction comparison was designed as a definitive efficacy test. Interpretation therefore needs to distinguish the measured question—participant satisfaction—from the broader research goal of informing a later study of outcomes related to PTSD and chronic pain.

3. Trial Design

The registry record describes a randomized, single-masked, parallel-group trial of Tai Chi and a Wellness program. The study is marked completed, with an enrollment of 42. Its registry phase is listed as NA. The identity of the masked party, the method used to generate the random assignment, and the allocation concealment procedures are not reported in the registry record.

The study summary describes a two-part project. The first part was intended to adapt, refine, and standardize two 12-week protocols for veterans with PTSD and chronic musculoskeletal pain, and to pilot remote delivery through videoconferencing. The second part was intended to assess the feasibility and acceptability of a remotely delivered randomized trial and its assessment procedures. The summary says information from the trial would help plan a larger randomized study comparing Tai Chi with Wellness. These aims frame the posted outcomes as feasibility-related evidence rather than as a conclusive clinical efficacy assessment.

Participants were assigned to a Tai Chi group or a Wellness group. The Tai Chi arm is described as receiving a standardized protocol adapted for veterans and administered by experienced VA Tai Chi instructors. The Wellness arm is described as receiving a program used by the investigators in other studies of veterans with chronic pain. The registry identifies both interventions as behavioral. Details about session frequency, attendance targets, adherence criteria, and the final delivery procedures are not reported in the registry record.

The primary outcome was participant satisfaction after treatment, at about 12 weeks. The record also posts secondary outcomes concerning treatment credibility, treatment expectancy, and completion of weekly log sheets. Although seven outcome measures are indicated in the record, results are posted for the primary outcome and three secondary outcomes. The registry record does not report analyses for the posted outcomes.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: CSQ data are not available for 3 participants in the Tai Chi Groups and 3 participants in the Wellness Group.

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 Participant Satisfaction Post Treatment With Interventions Being Tested, measured over Post-treatment (about 12 weeks).

The primary endpoint is participant satisfaction after treatment, assessed at about 12 weeks. Satisfaction was measured with the self-administered Client Satisfaction Questionnaire (CSQ), described as an 8-item scale. Individual responses range from 1 to 4, and higher scores are associated with greater satisfaction with treatment. The posted outcome is the mean score in each group, with standard deviations describing variation among participants’ scores.

Satisfaction is relevant to a feasibility study because it describes participants’ experience of the intervention. In general, satisfaction can help researchers judge whether an intervention and its delivery are acceptable enough to warrant further study. It is not, by itself, a measure of whether PTSD symptoms or chronic pain improved. The registry names PTSD and chronic pain as the conditions of interest, but the primary endpoint concerns satisfaction with the interventions being tested.

The posted primary-outcome groups each have 18 participants with CSQ data. The registry notes that CSQ data are unavailable for 3 participants in each group. The record does not report how missing CSQ responses were handled, whether any scale items were missing within otherwise available questionnaires, or whether the analysis used an intention-to-treat or another analysis population. Those omissions limit assessment of how representative the reported group means are of all participants assigned to each intervention.

7. Results Posted in the Registry

• Wellness Group: mean 3.40 versus 3.61 on control; difference -0.21 (95% CI -0.56 to 0.14), standardized effect d = -0.39; z-test p = 0.239.

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.

Credibility of Treatment

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Wellness Group: 55.6% (10/18) versus 57.9% (11/19) on control; risk difference -2.3 percentage points (95% CI -34.3 to 29.6), risk ratio 0.96 (0.55–1.69); unadjusted two-proportion z-test p = 0.886.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Wellness Group and the control. The interval gives the range of effects that remain compatible with the data.

Expectancy of Treatment

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Wellness Group: 22.2% (4/18) versus 21.1% (4/19) on control; risk difference 1.2 percentage points (95% CI -25.4 to 27.7), risk ratio 1.06 (0.31–3.60); unadjusted two-proportion z-test p = 0.931.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Wellness Group and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Completed the Weekly Log Sheet

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Wellness Group: 76.2% (16/21) versus 76.2% (16/21) on control; risk difference 0.0 percentage points (95% CI -25.8 to 25.8), risk ratio 1.00 (0.71–1.40); unadjusted two-proportion z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Wellness Group and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several aspects of feasibility and participant experience: treatment credibility, treatment expectancy, and completion of weekly log sheets. Taken together, the posted results do not establish a clear separation between the intervention groups across these measures. The estimates are uncertain, and the registry does not report analyses for the secondary endpoints. The overall pattern should therefore be read as descriptive rather than as a set of confirmatory conclusions.

These measures complement the primary satisfaction outcome but do not answer the same question. Credibility and expectancy concern participants’ views of treatment, while weekly log completion concerns an assessment procedure. Satisfaction is a post-treatment rating of the intervention. Considering these outcomes together can help frame the feasibility of a larger study, but none is a substitute for directly evaluating PTSD or chronic pain outcomes. The primary result and secondary measures also do not establish whether remote delivery is acceptable for all intended participants.

Secondary results generally carry less weight than a prespecified primary endpoint because multiple outcomes create more opportunities for chance findings, particularly when many comparisons are examined. The registry lists seven outcome measures, while results are posted for three secondary outcomes in addition to the primary endpoint. The intended hierarchy among all measures and any multiplicity adjustment are not reported in the registry record. The displayed unadjusted comparisons should therefore not be treated as independent confirmations of a treatment effect.

There is also variation in the number of participants included across posted secondary outcomes. The registry does not explain the reasons for these differing denominators or describe how missing observations were handled. That makes comparisons across endpoints less straightforward: apparent consistency or inconsistency may reflect differences in who contributed data as well as differences in the outcomes themselves. Overall, the secondary findings are best treated as exploratory information for planning assessment procedures and a future study, rather than as evidence of efficacy.

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

• Credibility of Treatment
• Expectancy of Treatment
• Percentage of Participants Who Completed the Weekly Log Sheet

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: each participant’s CSQ responses contribute to a score, and the registry reports a group mean and standard deviation. A mean describes the average score in a group. A standard deviation describes how dispersed individual scores are around that group average. It does not indicate how certain the mean is; uncertainty in a mean comparison is represented separately by a confidence interval.

The primary comparison is a mean difference, expressed as Wellness minus Tai Chi. With this direction, a negative estimate means the posted Wellness mean is lower than the posted Tai Chi mean. The observed estimate is -0.21. The direction of the comparison is important: reversing the group order would reverse the sign without changing the underlying difference in group scores. The estimate is unadjusted and based on posted summary statistics, not on an adjusted model described by the registry.

A confidence interval gives a range of values compatible with the data under the statistical method and its assumptions. It is not a range containing a known proportion of individual participants’ scores, and it is not a guarantee that the true effect falls within its endpoints. For the primary comparison, the interval spans zero. That indicates that the posted data do not sharply distinguish a negative group difference from no difference or a positive difference. The interval’s width is central to interpretation: a result may be statistically inconclusive while still allowing meaningful differences in either direction.

The unadjusted p-value is 0.239. In general, a p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, nor does it measure the size or practical importance of an effect. The registry does not report an analysis plan or adjusted analyses, so this p-value should be understood as an unadjusted comparison rather than a result incorporating a documented multiplicity procedure or covariate adjustment.

The primary outcome’s standard deviations, 0.51 and 0.56, describe within-group score variability. In general, variability affects precision: greater dispersion makes it harder to estimate a group difference precisely when other features of the design remain similar. The mean difference and its confidence interval combine information about the observed separation of group means and the uncertainty around that separation. They do not establish that the observed difference is clinically important. The registry does not provide a threshold for a meaningful difference on the CSQ.

The record also posts binary secondary outcomes, expressed as counts of participants meeting or having the recorded outcome. For binary outcomes, a risk difference compares the proportion with the outcome between groups. A confidence interval for a risk difference indicates uncertainty in that contrast; an interval spanning zero is compatible with no difference as well as differences in either direction. In general, binary outcomes with few events can yield particularly imprecise estimates. The registry posts no reported analyses for these secondary endpoints, so the posted comparisons should not be treated as adjusted or confirmatory findings.

The planning illustrations use assumptions stated in the registry record: a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use a specified fraction of the observed effect as the effect to detect. The primary-outcome illustrations give participants per arm. They are planning calculations based on the observed effect, not the trial’s original design justification. The original design assumptions are not reported in the registry record. In general, a significance level sets the threshold for a statistical test under its null model; power describes the chance of detecting an assumed effect under the planning assumptions if that effect is present. These properties depend on the assumed effect and other design inputs.

Over-dispersion is a general concern for count or binary outcomes when observed variation exceeds that expected under a chosen statistical model. In that setting, methods that assume less variation than is actually present may understate uncertainty. The registry does not report an over-dispersion assessment, a model for the binary endpoints, or adjusted analyses. This is a general methodological consideration, not a claim that over-dispersion occurred in this trial. For the continuous primary outcome, the posted mean and standard deviation offer descriptive information, but the registry does not report a model checking procedure or distributional assessment.

The registry notes missing CSQ data for participants in both groups. In general, complete-case summaries may be affected if participants with unavailable outcome data differ from participants with available data. Whether that concern applies depends on why data are missing and how missingness relates to outcome values and group assignment. Those reasons and the missing-data assumptions are not reported in the registry record. The posted means therefore describe participants with available CSQ data; the record does not establish how the missing observations were treated in any sponsor analysis.

The registry lists the trial as randomized and single-masked, but details needed to evaluate the randomization and masking procedures are not reported. Random assignment can support unbiased comparisons when implemented and analyzed appropriately, but it does not by itself eliminate uncertainty from missing data, limited precision, outcome measurement, or deviations from assigned treatment. Single masking can reduce some forms of bias, but the masked party and the masking procedures are not reported. The registry also lists seven outcome measures and posts results for the primary outcome and three secondary outcomes; the intended hierarchy and any multiplicity strategy are not reported.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the group difference. The posted primary mean difference is -0.21, and its confidence interval extends from a negative value to a positive value, crossing zero. This means the data are compatible with a difference favoring either group as well as with no average difference. The interval is not narrow enough to make the direction of the underlying difference clear.

The unadjusted p-value of 0.239 is consistent with that uncertainty, but it should not be interpreted as evidence that the two interventions are equivalent. Equivalence requires an appropriate design and a prespecified range of differences considered acceptably small; such a range is not reported in the registry record. A failure to distinguish the groups statistically can arise because the true difference is small, because the estimate is imprecise, or both. The posted results alone do not separate these possibilities.

The primary outcome is based on CSQ data available for 18 participants in each group, while the registry notes unavailable CSQ data for 3 participants in each group. The observed standard deviations are 0.51 for Tai Chi and 0.56 for Wellness. Both the available data and the score variability contribute to the uncertainty of the comparison. The registry does not report a precision target, a clinically important difference, or the original design assumptions, so there is no registry-based threshold against which to judge whether the estimate is sufficiently precise for a later efficacy decision.

In general, greater precision would require an estimate with less uncertainty, but increasing sample size is not the only consideration: measurement quality, missing outcome data, and the analysis method also matter. The planning illustrations show how required participants per arm change under assumed effects, but those figures do not remove the uncertainty in the observed trial estimate. They are prospective calculations based on stated assumptions, not additional evidence about the true satisfaction difference.

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 for the primary continuous outcome are expressed as participants per arm, not as a total across arms and not as total events. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario assumes the effect to detect is a stated fraction of the observed effect. These are planning assumptions; the registry record’s own original design assumptions and sample-size justification are not reported.

The 80% power column gives the planned participants per arm under which the calculation would have an 80% chance of detecting the assumed effect at the stated significance level, if the planning assumptions hold. The 90% power column expresses the corresponding calculation for a higher chance of detection. These are design targets, not guarantees about what a future trial will achieve. For the full observed effect, the illustration gives 103 participants per arm for 80% power and 137 participants per arm for 90% power. Planning for 75% of the observed effect gives 182 participants per arm for 80% power and 244 participants per arm for 90% power. Planning for 50% of the observed effect gives 409 participants per arm for 80% power and 547 participants per arm for 90% power.

The pattern reflects a general principle: smaller effects are harder to distinguish from random variation, so detecting them generally requires more participants when other assumptions remain fixed. The observed effect is uncertain, particularly in a feasibility trial, so these scenarios should be read as illustrations of how design needs depend on the effect chosen for planning. The registry does not report that the original trial was designed using these calculations. This is not observed power; it is a set of planning illustrations based on the observed effect and stated assumptions.

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 = -0.210; pooled standard deviation σ = 0.536.
2. n = 2 × (1.96 + 0.842)² × 0.536² / -0.210² = 102.1, rounded up to 103 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 <- -0.21                      # observed difference in means
sigma <- 0.535583793630838                     # 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(5693805)
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 = 103 (80% power), 137 (90% power)
 75% of observed effect: n per arm = 182 (80% power), 244 (90% power)
 50% of observed effect: n per arm = 409 (80% power), 547 (90% power)
power.t.test: 103.1 
Simulated power at n = 103 per arm: 0.803 (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 lists seven outcome measures and posts results for the primary endpoint and three secondary endpoints. It does not report a prespecified hierarchy for all outcomes, whether secondary results were intended to be confirmatory, or whether any multiplicity adjustment was planned or applied. When multiple outcomes are tested, the chance of at least one apparently unusual result can increase. In general, multiplicity procedures address that issue by adjusting interpretation or testing thresholds. Without a reported plan, the posted secondary comparisons should be viewed as exploratory and should not be assigned the same evidential weight as a single prespecified primary comparison.

The primary endpoint has missing CSQ data for 3 participants in the Tai Chi group and 3 participants in the Wellness group. The posted primary summaries use 18 participants in each group. The registry does not report why those data are unavailable, whether missingness occurred at the item or questionnaire level, or whether any imputation or sensitivity analysis was conducted. It also does not report a rule for defining a usable CSQ score. These details matter because missing outcome data can affect the estimate if availability is related to participants’ satisfaction or to their assigned intervention.

Denominators also differ across the posted secondary outcomes. The record does not explain whether this reflects outcome-specific availability, eligibility, or another reason. It does not report an analysis population, such as an intention-to-treat population, or say how participants who did not complete assessments were handled. The registry record does not report protocol deviations, treatment adherence analyses, or sensitivity analyses addressing missing outcomes.

The study is described as randomized and single-masked, but the identity of the masked party and details of randomization are not reported. The record also does not describe a statistical analysis plan, covariate adjustment, interim analyses, or a plan for multiplicity. These omissions do not demonstrate that such procedures were absent; they mean that they are not reported in the registry record. Readers should distinguish the results that are posted from methodological details that cannot be assessed from the registry information.

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 registry reports zero serious adverse events among 21 participants at risk in the Tai Chi group and zero among 21 participants at risk in the Wellness group. It also reports zero other adverse events in each group among 21 participants at risk, and zero deaths in each group. These are the recorded counts for the groups and categories listed in the registry.

Zero recorded events does not establish that an intervention has no risk. The safety figures describe what was reported for this trial, not every possible event or a guarantee about future use. The registry does not report the adverse-event definitions, collection procedures, severity criteria for non-serious events, or the specific observation period for these counts. It also lists no serious-event terms. Those reporting details are needed to understand the scope of surveillance and what qualified for each category.

The event counts should be interpreted alongside the feasibility purpose and the trial’s limited size. The registry record does not provide a comparative safety analysis or estimates of event rates with confidence intervals. Thus, the figures are descriptive registry reports, not precise evidence that the groups have identical safety profiles.

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

The result does show that post-treatment satisfaction scores were posted for both intervention groups, with a mean of 3.61 for Tai Chi and 3.4 for Wellness on the CSQ. The estimated mean difference, defined as Wellness minus Tai Chi, is -0.21. The confidence interval crosses zero, and the unadjusted p-value is 0.239. These statistics describe an uncertain group comparison: the posted data do not establish a clear difference in average satisfaction, but they also do not establish equivalence.

The result does not show whether Tai Chi or Wellness improves PTSD or chronic pain. Satisfaction is an experience-of-treatment outcome, not a direct symptom or pain outcome. The study summary describes a future efficacy trial as a goal, and the present trial’s stated purpose is to refine interventions and assess feasibility and acceptability. The registry results should not be interpreted as a definitive test of clinical benefit.

The findings also do not establish that remote intervention delivery is feasible for every participant or setting. The study summary describes remote adaptation and feasibility assessment, but the posted primary statistic concerns satisfaction. The registry record does not provide detailed measures of attendance, adherence, recruitment performance, retention criteria, or technical difficulties. Those aspects cannot be inferred from the satisfaction result alone.

The planning calculations offer possible sample sizes under stated assumptions and alternative effect sizes. They do not show how many participants would be sufficient under every plausible future design, and they do not validate the observed effect as the best planning value. A future efficacy study would need clearly specified outcomes, analysis methods, and design assumptions suited to its research question. The original design assumptions for this trial are not reported in the registry record.

Finally, the posted results are constrained by missing CSQ data and by the absence of reported analysis details. The record does not explain missingness, identify the analysis population, or report adjusted analyses. The appropriate conclusion is therefore limited: the registry presents preliminary group summaries for satisfaction and related feasibility measures, with uncertainty that does not support a decisive between-group claim.

17. Why This Trial Matters Statistically

This trial illustrates the distinction between a feasibility study and an efficacy study. Its stated purpose was to refine remotely delivered interventions and assessment procedures, assess feasibility and acceptability, and inform a future randomized efficacy trial. Its primary posted endpoint—satisfaction—fits that preparatory purpose, but it is not the same as measuring whether PTSD or chronic pain outcomes improve.

Statistically, the mean difference and confidence interval are useful because they show both the direction of the observed contrast and its uncertainty. The estimate favors a higher observed mean in the Tai Chi group, but the interval crosses zero and the unadjusted p-value does not establish a clear difference. This is more informative than treating a result as simply positive or negative. It also demonstrates why a non-significant comparison should not be mistaken for proof that treatments are equivalent.

The planning illustrations make another important point: required sample size depends strongly on the effect a later study aims to detect. Smaller assumed effects require more participants under otherwise fixed assumptions. Yet the observed effect in a feasibility study is itself uncertain, so it should not be adopted uncritically as the expected effect for a definitive study. A range of plausible planning assumptions is more informative than relying only on one estimate.

Finally, the registry’s missing-data and analysis-plan details matter. Missing primary outcome data and differing secondary-outcome denominators affect how confidently the posted summaries can represent the randomized groups. A future trial can be better interpreted when its outcome hierarchy, analysis population, missing-data approach, and multiplicity strategy are clearly reported. The current record provides useful preliminary information, while also showing why transparent reporting is essential to assess precision and evidential strength.

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 primary result is based on CSQ data available for 18 participants in each group, and the registry reports that data are unavailable for 3 participants in each group. Reasons for missingness and the handling of missing outcomes are not reported. If missingness is related to satisfaction or participation, the posted group means may not fully represent all participants assigned to the interventions.

The registry reports a completed feasibility study but does not report the original sample-size rationale, the statistical analysis plan, or a prespecified clinically important difference for satisfaction. The confidence interval around the primary comparison crosses zero, leaving uncertainty about the direction and size of the group difference. The planning figures are based on the observed effect and stated assumptions, not on the trial’s original design assumptions.

The identity of the masked party and details of randomization are not reported. The registry also does not describe the analysis population, treatment adherence, protocol deviations, or adjustment for covariates. Those omissions limit assessment of how the randomized design was implemented and how the reported summaries relate to assigned treatment.

Results are posted for three secondary endpoints, while the record lists seven outcome measures. The intended hierarchy of outcomes and any multiplicity strategy are not reported. Secondary denominators vary, and the registry does not explain why. Their unadjusted results are consequently limited as evidence for a treatment contrast.

The primary outcome measures satisfaction, not PTSD symptoms or chronic pain. The registry record does not provide detailed results for those clinical outcomes in the posted results. Safety reporting is also limited to event counts; definitions, surveillance procedures, and observation periods are not reported. These trial-specific limitations make the registry findings most appropriate as preliminary feasibility information rather than a definitive clinical evaluation.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Feasibility of Remote Tai Chi — NCT05693805.
• Registry record last updated 2026-05-20; status last verified 2026-05.
• Results first posted 2025-11-28.
• 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

NCT05693805, titled “Feasibility of Remote Tai Chi,” is listed as completed. The registry describes a randomized, single-masked, parallel-group study with enrollment of 42 and a registry phase of NA. Boston University is listed as sponsor. The conditions are PTSD and chronic pain.

The trial compared a Tai Chi intervention with a Wellness program. The study summary describes adapting both interventions for remote delivery and using the study to inform a future efficacy trial. The primary outcome was post-treatment satisfaction, measured by the CSQ at about 12 weeks. The posted group means were 3.61 for Tai Chi and 3.4 for Wellness; the unadjusted mean difference was -0.21, with a confidence interval that crossed zero.

Secondary outcomes concern credibility, expectancy, and weekly log completion. The registry reports zero serious adverse events, zero other adverse events, and zero deaths in each group. Missing-data methods, the original design assumptions, and a statistical analysis plan are not reported in the registry record.