Treatments for Improving Mood in Depressed Teens-3: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Treatments for Improving Mood in Depressed Teens-3 (NCT03831360), a randomized na study. The primary outcome is Acceptability.

2. Clinical Question

The registry brief describes the study as a randomized clinical trial of yoga versus group CBT for adolescents with depression. The primary endpoint is framed around whether participants engage with the assigned program enough to meet a prespecified attendance threshold. That makes the main question one of feasibility and acceptability in this study, rather than a definitive comparison of clinical benefit.

3. Trial Design

The registry record describes a randomized, parallel-group trial with single masking. It lists the study as completed and gives enrollment as 30. The phase field is listed as NA, while the brief summary calls the study a phase 3 randomized clinical trial. These are different descriptions in the record; further information reconciling them is not reported in the registry record.

The two behavioral interventions were Hatha yoga and group CBT. Each arm description specifies a 12-week program. The posted primary endpoint also uses a 12-week timeframe, counting participants who attended at least 8 of 12 possible classes. The registry lists Brown University as sponsor. The recorded study start was 2019-10-21, and the primary completion date was 2021-09-29.

The primary endpoint is reported as a participant count. The Hatha yoga arm lists 15 participants and 11 meeting the attendance threshold; the group CBT arm lists 15 participants and 13 meeting it. Those counts are the basis for the posted comparison. The registry does not report the randomization procedure, allocation concealment, the identity of the masked party, or details about whether outcome assessment was masked. Those aspects of the trial design are therefore not reported in the registry record.

A secondary outcome is the Quick Inventory of Depression - Adolescent Version - Clinician Rating (QIDS-A-CR), reported as a mean score with standard deviation for baseline to post intervention (month 3). The reported outcome counts for this measure differ from the arm counts listed for the primary outcome. The record does not explain the difference, nor does it report how missing outcome data were handled. No inferential analyses are listed as reported analyses in the registry record.

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.

Population: All participants who were randomized.

6. Primary Endpoint

The registry lists the primary outcome as Acceptability, measured over 12 weeks.

The primary endpoint measures attendance, not symptom change. Acceptability is operationalized as the number of participants who attended at least 8 of the 12 possible classes during the 12-week intervention. The record states a target of 70% or greater. The reported counts are 11 participants for Hatha yoga and 13 for group CBT, with 15 participants listed in each arm for this endpoint.

An attendance threshold turns participation into a practical indicator of whether people engage with a program. This can be useful in an adaptation or pilot study: if participants do not attend, a larger evaluation may be difficult to conduct as planned. However, attendance alone cannot establish why someone did or did not attend, whether the program was acceptable in other respects, or whether symptoms improved. It also does not measure the quality or amount of participation within a class.

The target gives the endpoint a benchmark for interpretation, but the posted record does not describe the justification for selecting that threshold or target. The primary result should therefore be read as an observed count against a stated acceptability criterion, not as a complete assessment of feasibility or clinical value. The QIDS-A-CR is a separate secondary measure intended to describe depression scores over the intervention period; it does not change what the primary attendance endpoint measures.

7. Results Posted in the Registry

• Group CBT: 86.7% (13/15) versus 73.3% (11/15) on control; risk difference 13.3 percentage points (95% CI -14.9 to 41.6), risk ratio 1.18 (0.82–1.70); unadjusted two-proportion z-test p = 0.361.

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.

Quick Inventory of Depression - Adolescent Version - Clinician Rating (QIDS-A-CR)

• 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:
  • Group CBT: mean 8.23 versus 6.92 on control; difference 1.31 (95% CI -2.10 to 4.72), standardized effect d = 0.31; z-test p = 0.451.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group CBT and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists one secondary outcome: the Quick Inventory of Depression - Adolescent Version - Clinician Rating (QIDS-A-CR). The posted outcome summary reports scores from baseline to post intervention (month 3), with means and standard deviations for the two arms and a mean-difference comparison. No other secondary outcome result is described in the record, although the registry lists seven outcome measures overall.

In broad terms, the secondary result does not establish a clear separation between arms on the clinician-rated score. Its confidence interval includes zero, and the unadjusted p-value is 0.451. This pattern is not the same as the attendance result: attendance was the primary acceptability measure, whereas the QIDS-A-CR is a symptom score. The secondary finding neither confirms nor explains the observed attendance pattern, and it should not be treated as a substitute for the primary endpoint.

Secondary outcomes usually have a supporting role in interpretation. They can offer context about domains not captured by the primary endpoint, but conclusions based on them are often less secure when there are multiple outcomes, limited observations, or no clearly reported analysis plan. Testing or examining many outcomes can increase the chance that an apparently notable result arises by chance. The registry record does not report a multiplicity strategy or a hierarchy of secondary hypotheses, so the posted secondary result should be treated as exploratory rather than as a stand-alone basis for a broad conclusion.

The record does not report analyses for the other listed outcome measures. Consequently, the overall secondary-outcome pattern cannot be fully characterized from the registry record. The available secondary result can be read alongside the primary attendance result as additional descriptive information, but it does not resolve the uncertainty in the primary comparison or support a claim of clinical effectiveness.

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

• Quick Inventory of Depression - Adolescent Version - Clinician Rating (QIDS-A-CR)

9. Statistical Interpretation

10. Statistical Methods Explained

The statistical summaries address two kinds of outcomes. The primary endpoint is a count of participants who met an attendance threshold. The secondary QIDS-A-CR endpoint is a mean score accompanied by a standard deviation. These outcome types call for different summaries: counts and proportions describe the attendance measure, while means and variability describe the score. General statistical explanations below clarify how to read those summaries; details of the trial's original analysis plan are not reported in the registry record.

What does the attendance comparison summarize?

For each arm, the posted results give the number of participants meeting the attendance criterion and the number listed for the endpoint. A risk difference expresses the contrast in the proportions meeting that criterion between arms. In this record, the contrast is expressed as group CBT relative to Hatha yoga, and the posted estimate is 0.133. The direction is positive because the observed proportion meeting the threshold is higher in group CBT. A risk difference is an absolute contrast in proportions, rather than a relative multiplier.

The posted comparison also includes a p-value. In general, a p-value describes how compatible observed data are with a specified null model, under the assumptions used for the calculation. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of a difference. The registry lists p = 0.361 for the unadjusted attendance comparison. No reported analysis or adjusted model is listed in the record, so the summary should not be mistaken for a model-based or covariate-adjusted estimate.

How should a confidence interval be read?

In general, a confidence interval describes a range of estimates that are reasonably compatible with the data under the method's assumptions. It conveys uncertainty around an estimate; a wider interval indicates less precision than a narrower interval. For the attendance comparison, the interval extends to both sides of zero. Zero represents no risk difference, so the interval includes no difference as well as differences in either direction. This means the observed positive contrast is not estimated precisely enough to rule out other plausible contrasts.

A confidence interval does not assign a probability to a particular treatment effect, nor does it guarantee that the true value lies within its endpoints. Its interpretation depends on the statistical method and assumptions. The registry record does not report the method used to construct the displayed interval, so the interval is best interpreted as the posted uncertainty summary rather than as evidence about unreported modeling choices.

What does the secondary mean difference represent?

The secondary outcome is reported as a mean QIDS-A-CR score and standard deviation in each arm. A mean difference compares those arm means. The posted comparison is 1.31 for group CBT relative to Hatha yoga; the arm means are 8.23 and 6.92, respectively. The standard deviation describes variability of individual scores around an arm's mean. It is not the standard error of the mean and does not describe uncertainty in the same way as a confidence interval.

The reported confidence interval for the mean difference runs from -2.1 to 4.72, including zero. In general, an interval crossing zero is compatible with no mean difference under the specified method, as well as differences in either direction. The posted unadjusted p-value is 0.451. The record does not list a reported inferential analysis for this outcome, so the result should be read as an unadjusted comparison rather than a confirmed result from a documented analysis plan.

Why might statistical methods matter for counts?

General methods considerations depend on the outcome's data structure. For binary participant outcomes, methods may compare proportions directly or use models for binary responses. Some methods account for covariates or other design features, while simple unadjusted comparisons do not. The registry does not report which inferential procedure was planned or used, beyond the posted unadjusted summaries. It is therefore not appropriate to infer a particular model, correction, or test from the numbers alone.

Over-dispersion is a general concern when counts vary more than a model assumes. It can make standard errors too small if the extra variability is ignored. The primary endpoint is a participant-level attendance threshold, not a reported count of repeated events per person, and the record supplies no dispersion estimate or model details. There is no basis in the registry record for asserting that over-dispersion was assessed or that a particular correction was applied.

What do the analysis records leave unknown?

The record lists seven outcome measures and one posted secondary outcome, but no reported analyses. It does not report whether analyses followed intention-to-treat, per-protocol, or another population definition. Nor does it describe how participants with missing follow-up measurements were treated, whether any covariates were selected in advance, or whether interim analyses took place. These details can affect the interpretation of inferential results and should not be reconstructed from the arm summaries.

The sample-size illustrations use a normal approximation and equal allocation between the two arms, with a two-sided significance level of 0.05. They are based on the observed effect and show planning values for different fractions of that effect. Those assumptions describe the illustration, not necessarily the original trial design. The original design assumptions and sample-size justification are not reported in the registry record.

11. Confidence Intervals and Precision

Precision concerns how narrowly the results locate a plausible value for the underlying contrast. For the primary attendance comparison, the posted risk-difference interval extends to both sides of zero. It therefore allows no difference as well as contrasts in either direction, and its span indicates that the observed estimate is uncertain. The point estimate alone, 0.133, should not be read as a stable estimate of the difference that would necessarily appear in a larger study.

The secondary QIDS-A-CR mean-difference interval extends from -2.1 to 4.72. Because it includes zero, it is compatible with no mean difference as well as values favoring either arm in the direction of the score contrast. Its width relative to the observed estimate also underscores that the available data do not locate the underlying mean difference precisely. The posted p-value of 0.451 is consistent with substantial uncertainty, but the interval is more informative about the range of contrasts that remain compatible with the data.

Both arm-level outcome summaries come from a pilot-scale trial, and the number of participants listed for each endpoint is limited. With relatively few observations, estimates can be sensitive to individual outcomes, and confidence intervals may be broad. That does not mean the estimates are uninformative: they describe the observed sample and help characterize uncertainty. It does mean that absence of a clearly separated result should not be equated with evidence of equivalence.

Intervals are conditional on the methods and assumptions used to calculate them. The registry record does not report the original analysis plan or a detailed interval-construction method. Thus, precision should be understood from the posted intervals and counts without assuming unreported adjustment, missing-data handling, or a particular inferential model.

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 illustrations are planning scenarios based on the observed effect, not the original trial's documented design assumptions. For these two-arm comparisons, the displayed values are participants per arm, not total participants and not total events. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario considers detecting the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were the true effect and the model assumptions held. The 90% power column gives the corresponding planning number for a 90% chance. These are design calculations; they do not say how likely the trial's observed result was or whether the observed effect is real.

For the primary attendance comparison, the illustration lists 141 participants per arm for planning around 100% of the observed effect, 266 per arm for 75% of that effect, and 631 per arm for 50% of that effect at the 80% power level. The corresponding 90% power values are 188, 355, and 844 participants per arm. For the secondary QIDS-A-CR comparison, the 80% power values are 167, 296, and 666 participants per arm across those same effect fractions; the 90% power values are 223, 396, and 891 participants per arm.

Smaller effects are harder to distinguish from random variation, so the planning illustrations require more participants per arm as the effect fraction gets smaller. These figures are planning illustrations, not observed power. The original trial's sample-size assumptions and justification are not reported in the registry record.

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 = 0.733; treatment proportion p₁ = 0.867; average p̄ = 0.800.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5657 = 1.1087.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5578 = 0.4694.
4. n = (1.1087 + 0.4694)² / (0.1333)² = 140.1, rounded up to 141 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 <- 0.733333333333333                          # control proportion
p1 <- 0.866666666666667                          # 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(3831360)
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 = 141 (80% power), 188 (90% power)
 75% of observed effect: n per arm = 266 (80% power), 355 (90% power)
 50% of observed effect: n per arm = 631 (80% power), 844 (90% power)
power.prop.test: 140.1 
Simulated power at n = 141 per arm: 0.806 (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

Several elements needed to evaluate the full analysis strategy are not reported in the registry record. The record lists seven outcome measures but posts one secondary outcome summary and lists no reported analyses. It does not state which outcome was designated primary in an analysis plan beyond the posted acceptability endpoint, how secondary outcomes were prioritized, or whether formal hypotheses were prespecified for each measure.

Multiplicity arises when several outcomes, comparisons, time points, or analyses are considered. In general, the more opportunities there are to identify a result, the more likely it is that at least one result may appear notable by chance. Statistical strategies can address this, for example by adjusting tests or specifying a hierarchy in advance. Whether such a strategy was used is not reported in the registry record. The posted p-values are unadjusted, so they should not be interpreted as multiplicity-controlled evidence.

Missing-data handling is also not described. The outcome summary lists 15 participants per arm for attendance, while the QIDS-A-CR summary lists 12 for Hatha yoga and 13 for group CBT. The registry does not explain why those secondary outcome counts differ from the primary endpoint counts, whether measurements were unavailable, or how any missing observations were handled. No assumptions about the reasons for missingness or the analysis of incomplete outcomes can be made from the record.

The analysis population is not reported in the registry record. It is therefore unclear whether the posted outcomes represent all randomized participants, participants with available data, or another defined group. The record also does not describe protocol deviations, adherence-based exclusions, or the handling of participants who did not complete the assigned program. These omissions matter because different analysis populations can answer different questions.

Finally, an interim-analysis plan, stopping rules, and the original statistical analysis plan are not reported in the registry record. Without those details, the posted summaries can be interpreted as the results recorded for the outcomes, but not as a complete account of all analytic decisions or checks.

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 non-serious adverse event terms

The adverse-event record lists no serious adverse events in either arm. It reports no deaths in either arm. For other adverse events, the record lists 1 participant in the Hatha yoga group and 2 participants in the group CBT group. These are the posted figures for the groups at risk as recorded in the adverse-event data.

These counts describe events recorded in this trial; they do not establish that an intervention caused an event, or that an event was unrelated to an intervention. The record does not provide the terms for the other adverse events, and it lists no top serious-event terms. It also does not give detailed information about event severity, timing, duration, or how events were assessed. Those details are not reported in the registry record.

When reading safety counts, the number of observed events must be considered alongside the amount of follow-up and the completeness of reporting. A trial of this size cannot rule out uncommon harms, and zero recorded serious events does not demonstrate that serious events cannot occur. These data should be read as the adverse-event record for this study, not as a comprehensive safety assessment or a comparison with enough precision to establish different risk between the interventions.

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

The clearest descriptive finding is that most participants listed in each arm met the study's attendance threshold, with a higher count in group CBT than in Hatha yoga. The primary comparison is uncertain: its interval includes zero and its unadjusted p-value is 0.361. The result therefore does not establish a reliable difference in attendance between the groups. It also does not establish that attendance was the same.

The attendance endpoint has a specific interpretation. It indicates whether participants attended at least 8 of 12 possible classes. It does not capture other dimensions of acceptability, such as preferences, satisfaction, perceived burden, or reasons for missed sessions. Nor does the attendance result establish improvement in depression. The secondary QIDS-A-CR score addresses a different question, and its comparison also remains uncertain.

The record supports a limited account of a randomized comparison of two 12-week behavioral programs in adolescents with depression. It does not provide enough information to conclude that one intervention is more effective, more acceptable overall, or safer than the other. The posted outcomes are not a basis for medical advice or treatment decisions. They are observations from this particular study, with uncertainty and reporting limitations.

The record calls the study an adaptation and pilot study, which is consistent with treating the estimates as preliminary. Pilot-scale data can inform planning and expose practical questions, but estimates may be imprecise and may not generalize beyond the studied setting or participants. Details about recruitment, participant characteristics, delivery fidelity, and broader generalizability are not reported in the registry record.

Accordingly, the findings should be interpreted as descriptive evidence about attendance and a secondary symptom-score summary in this trial. They do not prove benefit, harm, equivalence, or the absence of an effect. A stronger conclusion would require a clearly documented analysis plan, sufficient precision for the question of interest, and fuller reporting of study methods and outcomes.

17. Why This Trial Matters Statistically

This trial illustrates why pilot outcomes and clinical outcomes should be distinguished. The primary endpoint measures whether participants attend a specified share of classes, making it relevant to engagement and feasibility. The secondary clinician-rated score addresses depression symptoms. Keeping those questions separate prevents an attendance difference from being mistaken for a difference in clinical response.

The example also shows how an estimate and its uncertainty should be read together. The observed attendance count is higher in group CBT, but the interval for the comparison includes zero. The estimate gives the direction and scale of the observed contrast; the interval communicates that the underlying difference is not tightly determined by these data. A p-value alone cannot convey that range of uncertainty or establish equivalence.

Planning illustrations can help show how demanding a future study might be if investigators want to detect effects smaller than those observed in a pilot. Here, the illustrated number of participants per arm rises as the effect fraction decreases. That relationship is a general consequence of trying to distinguish smaller signals from random variation. The values are conditional on the stated planning assumptions and are not evidence that the observed effect will persist.

Finally, the record highlights the value of transparent reporting. The absence of a reported analysis plan, analysis population, multiplicity approach, and missing-data method limits how confidently the posted comparisons can be interpreted. Statistical results are most useful when readers can connect the outcome definitions, planned methods, participant flow, and estimates. This trial offers a focused case for reading descriptive results carefully without turning preliminary comparisons into definitive claims.

18. Limitations

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

Several limitations specific to this trial constrain interpretation. The registry gives limited information about the participants beyond adolescents with depression. Eligibility criteria, participant characteristics, recruitment methods, and study setting are not reported in the registry record. Without those details, it is difficult to judge how closely the participants resemble other adolescent populations or whether the results may apply beyond the trial context.

The registry describes the study as an adaptation and pilot study, and the arm counts are small. The estimates are consequently imprecise, as reflected in the posted intervals. The observed attendance difference should not be assumed to represent a stable difference in a larger study. The record does not report a sample-size justification for the original design.

Intervention details are limited to the names of the programs and their 12-week duration. The record does not report session frequency, instructor qualifications, adherence to treatment manuals, or treatment fidelity. It is also not clear from the record what single masking means in practice or who was masked. These details matter for understanding how the interventions were delivered and how outcomes may have been assessed.

The secondary score has fewer participants listed than the primary outcome, but the reason is not reported. The missing-data approach, analysis population, and handling of protocol deviations are also not reported. The registry lists seven outcome measures but posts only one secondary outcome summary, and no reported analyses are listed. A multiplicity plan and the original statistical analysis plan are not reported either.

Finally, the adverse-event record gives counts but little descriptive detail about event types or assessment. No serious events or deaths are listed, but the study's size and the available reporting do not support broad safety conclusions. These limitations do not invalidate the posted observations; they define the boundaries of what can be concluded from the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Treatments for Improving Mood in Depressed Teens-3 — NCT03831360.
• Registry record last updated 2022-06-02; status last verified 2022-05.
• Results first posted 2022-06-02.
• 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

The registry record describes a completed, randomized, parallel-group study comparing 12 weeks of Hatha yoga with 12 weeks of group CBT for adolescents with depression. Enrollment is listed as 30, and the primary endpoint is acceptability, defined by attending at least 8 of 12 possible classes. The posted attendance counts are 11 of 15 for Hatha yoga and 13 of 15 for group CBT.

The unadjusted primary comparison is uncertain. The registry also posts a secondary QIDS-A-CR score summary for baseline to post intervention (month 3), with a mean-difference interval that includes zero. No reported analyses are listed. The record does not report the original sample-size rationale, missing-data methods, analysis population, or multiplicity approach. The findings are best read as preliminary summaries of attendance and a secondary symptom score, not as definitive evidence of comparative effectiveness.