Predict the Best Level of Care Placement for Each Child's Behavioral Health Needs - Efficacy Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Predict the Best Level of Care Placement for Each Child's Behavioral Health Needs - Efficacy Study (NCT06815562), a randomized na study. The primary outcome is Mean Difference in Average Domain Z-scores Across Raters Within Two Weeks on the Clinical Scale of the Treatment Outcome Package (TOP-CS) Between a) Baseline and b) Follow-up..

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group efficacy study with no masking. The study compares access to Placement Success Predictor results with no access to those results. Its stated enrollment is 213. The listed arms distinguish experimental and control groups within child and adolescent samples, so outcomes are reported separately for those populations rather than as one combined estimate.

PSP is described as a clinical decision support tool that provides placement-specific predictions about the likelihood of a youth having a good outcome in each placement type. The intervention is access by clinical team members to the youth’s site-specific prediction scores. The registry does not describe the clinical decisions made after teams received scores, whether placements differed between conditions, or how closely teams used the predictions.

The primary measure is assessed at baseline, within 2 weeks of study start, and at follow-up approximately 60-120 days later. The brief study description refers to a 3-month follow-up. The registry status is completed, with a start date of 2025-02-03 and primary completion date of 2026-01-26. A phase is listed as NA.

The record does not report the randomization sequence method, allocation concealment, stratification, site count, or the protocol’s original sample-size justification. It also does not report a detailed statistical analysis plan or the analysis populations. Those omissions limit how fully the reported group summaries can be connected to the planned design and intended treatment effect.

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 Mean Difference in Average Domain Z-scores Across Raters Within Two Weeks on the Clinical Scale of the Treatment Outcome Package (TOP-CS) Between a) Baseline and b) Follow-up., measured over At baseline (within 2 weeks of study start) and approximately 60-120 days later.

The primary endpoint is the mean difference in average domain z-scores across raters on the Clinical Scale of the Treatment Outcome Package (TOP-CS), between baseline and follow-up. Baseline is within 2 weeks of study start, and follow-up is approximately 60-120 days later. The Child Treatment Outcome Package has 48 items and assesses 13 domains for children ages 3-18; the Adolescent TOP-CS has 58 items and assesses 12 domains for adolescents ages 11-21. The assessment covers the youth’s past 2-week experience in areas such as depression, violence, and suicidality. Scores are risk-adjusted for case-mix variables assessed on the companion TOP-Case Mix form.

A domain z-score of 0 represents the general population mean. Domain z-scores are averaged to form a participant-level summary, then summarized across raters. Higher, more positive average z-scores indicate greater symptom severity and lower behavioral well-being. A negative mean difference from baseline to follow-up indicates improvement, while a positive difference indicates worsening on this scale.

This repeated measure is intended to capture change in behavioral health symptoms over the follow-up period. It is relevant to the trial’s stated question because the hypothesis concerns youth outcomes after clinical teams gain access to placement predictions. The registry does not report the endpoint’s confidence level or a detailed rule for handling multiple raters.

7. Results Posted in the Registry

• Experimental, Child Sample: mean 0.45 versus 0.14 on control; difference 0.31 (95% CI -0.75 to 1.37), standardized effect d = 0.13; z-test p = 0.565.
• Experimental, Adolescent Sample: mean -0.06 versus 0.14 on control; difference -0.20 (95% CI -0.61 to 0.21), standardized effect d = -0.28; z-test p = 0.341.
• Control, Adolescent Sample: mean -0.20 versus 0.14 on control; difference -0.34 (95% CI -0.90 to 0.22), standardized effect d = -0.21; z-test p = 0.232.

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.

Mean Difference Between the Average Risk-adjusted Predicted TOP-CS Total Score Across Raters at Study Baseline and the Actual Average TOP-CS Total Score Across Raters at Follow-up

• 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:
  • Experimental, Child Sample: mean -32.90 versus -36.80 on control; difference 3.90 (95% CI -8.37 to 16.17), standardized effect d = 0.16; z-test p = 0.533.
  • Experimental, Adolescent Sample: mean 4.67 versus -36.80 on control; difference 41.47 (95% CI 31.43 to 51.51), standardized effect d = 2.26; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Experimental, Child Sample and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Experimental, Adolescent Sample than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary outcome: the difference between the risk-adjusted predicted TOP-CS total score across raters at baseline and the actual average TOP-CS total score across raters at follow-up. It is conceptually related to the primary outcome because both use TOP-CS information and compare baseline-related expectations with follow-up outcomes. However, it is not the same measure as the primary average domain z-score change. The score scale and comparison therefore require separate interpretation.

Across the secondary endpoint, the child experimental and control group estimates are in a similar direction, while the adolescent estimates differ in direction. The posted secondary comparisons also show a child interval that includes zero and an adolescent estimate with a much narrower interval excluding zero. That apparent adolescent contrast is not a reliable basis for an efficacy conclusion: its comparator input comes from the child control sample, not the adolescent control arm. The group summaries and the contrast are therefore not aligned for that age group.

The secondary pattern does not resolve the uncertainty in the primary result. It uses a different outcome definition, and the adolescent comparison problem affects interpretation. In addition, the registry lists no reported sponsor analyses for the secondary endpoint. The secondary estimates should be viewed as exploratory descriptive information rather than independent confirmation of the primary finding.

Unadjusted secondary results carry less weight because a study may examine several outcomes and group comparisons, creating more opportunities for apparently notable results to arise by chance. The registry does not describe a multiplicity adjustment, a prespecified hierarchy among outcomes, or a plan for selecting which secondary analyses would be confirmatory. The secondary outcome may help illustrate how the record summarizes related scores, but it cannot substitute for a correctly specified primary comparison or a reported analysis plan.

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

• Mean Difference Between the Average Risk-adjusted Predicted TOP-CS Total Score Across Raters at Study Baseline and the Actual Average TOP-CS Total Score Across Raters at Follow-up

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is an average z-score rather than a count or a binary event. A mean summarizes the central value of such measurements, while the standard deviation describes how spread out individual observations are around that mean. The reported group means and standard deviations therefore describe average change and variability within each listed arm. They do not, by themselves, provide a direct estimate of how much an individual youth changed.

The endpoint’s direction matters. The registry defines more positive average z-scores as greater symptom severity and lower behavioral well-being. For the within-person baseline-to-follow-up difference, a negative value indicates a reduction in severity, and a positive value indicates an increase. This direction should not be confused with the sign of a between-group estimate: that sign depends on which group is subtracted from which. The registry’s comparison values should be interpreted alongside the named groups and the component means, not as standalone indicators of improvement.

A confidence interval expresses uncertainty around an estimated contrast. It gives a range of values compatible with the estimate under the method used, and wider intervals indicate less precision. When an interval spans zero, the posted result is compatible with no difference as well as with effects in either direction. The registry does not state the confidence level used for these intervals, so it should not be assumed from the record. In the child primary comparison, the interval extends from -0.746 to 1.366. In the adolescent primary comparison, it extends from -0.612 to 0.212, but the adolescent comparison inputs do not match the adolescent control group.

A p-value describes how unusual the data would be under a specified null model, conditional on the statistical method and assumptions. It is not the probability that the null hypothesis is true, nor does it quantify the probability that the intervention is beneficial. The primary comparison p-values are unadjusted. A p-value alone does not show the size or practical importance of an effect; the estimate and its interval are needed to understand magnitude and uncertainty. The registry does not report a sponsor-authored analysis for the primary outcome.

Because allocation was randomized, a correctly conducted comparison can support causal interpretation within the enrolled study population, subject to the design and analysis assumptions. Randomization does not automatically resolve issues such as missing outcomes, departures from assigned treatment, or mismatched analysis groups. The record lists no masking, so clinical teams and participants were not described as masked to condition. The registry does not report whether outcome raters were masked, nor does it give details about adherence to the assigned condition or treatment switching.

The trial separates child and adolescent samples. Separate estimates can be useful when age-appropriate instruments differ, as the Child TOP-CS and Adolescent TOP-CS have different item and domain counts. However, the registry does not report a formal test of interaction or a prespecified subgroup analysis plan. The separate results should therefore not be treated as proof that treatment effects differ by age group. Also, the adolescent primary comparison uses the child control mean as its reference input, rather than the adolescent control mean. This limits interpretation of that contrast even though arm-specific adolescent summaries are listed.

Standard deviations are relevant to precision because variability affects how well a mean can be estimated. Larger variability can make an estimated contrast less precise when the number of observations is unchanged. Differences in spread across the posted arms are apparent, but the registry does not report methods for handling possible non-normality, influential observations, or unequal variances. No distributional checks or robust-model details are reported.

The sample-size illustrations are not descriptions of the study’s original design calculation. They use an observed effect and the stated planning assumptions. Such calculations are useful for illustrating the scale of a future study under those assumptions, but their results depend on the observed effect being a sensible planning target. In particular, a small observed effect can produce large planning counts, while unstable or misaligned estimates can make the illustration unsuitable for design decisions. The registry does not report the original sample-size justification or whether any interim analyses were planned.

Multiplicity is another statistical concern because the record includes a primary outcome, a secondary outcome, and separate child and adolescent results. Repeated testing can increase the chance of finding an apparently unusual result by chance if many results are examined. The registry does not report an adjustment strategy or a hierarchy for interpreting these analyses. The secondary outcome also has no sponsor-reported analyses listed. These limitations argue for treating the individual unadjusted comparisons as descriptive evidence rather than a complete confirmatory analysis.

11. Confidence Intervals and Precision

The primary confidence intervals communicate substantial uncertainty around the posted contrasts. For the child sample, the estimate is 0.31 and the interval ranges from -0.746 to 1.366. Because the interval includes zero and extends in both directions, the posted estimate does not sharply distinguish between a contrast favoring one group, no contrast, or a contrast favoring the other group. The unadjusted p-value is 0.565, which is also not strong evidence against a null comparison under the reported unadjusted test.

For the adolescent sample, the posted estimate is -0.2 and the interval ranges from -0.612 to 0.212. Its span also includes zero. More importantly, the comparison’s control input is 0.14, the child control mean, while the adolescent control arm mean is -0.2. The interval therefore does not provide a clean measure of uncertainty for the intended adolescent experimental-versus-control contrast. The arm-level summaries remain descriptive, but the posted contrast should be interpreted cautiously.

Confidence intervals are more informative than a point estimate alone because they show the range of estimates compatible with the data and method. They do not capture every source of uncertainty, such as missing data, measurement limitations, analysis choices, or whether the intended comparison was constructed correctly. The registry does not report the confidence level, a detailed model, or an adjusted estimate. The available intervals should therefore be read as precision summaries for the posted unadjusted comparisons, not as a complete account of uncertainty about PSP’s effect.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size illustrations give participants per arm, not total participants and not total events. This is a continuous-outcome study, so the displayed planning counts refer to participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect set to the stated fraction of the observed effect. The registry does not report the trial’s own original design assumptions or sample-size justification.

The 80% power column describes the planned number of participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the other assumptions hold. The 90% power column describes the corresponding count for a design with a 90% chance. These are design probabilities for hypothetical future studies, not probabilities that the posted study result is true.

Rows that plan for 100% of the observed effect use the full observed estimate as the target; rows for 75% and 50% plan for smaller effects. Smaller effects are harder to distinguish from random variation, so they require more participants under otherwise unchanged assumptions. The figures vary by endpoint and comparison, reflecting different observed estimates and variability. In particular, estimates with uncertain or mismatched comparisons should not be treated as dependable design targets merely because a planning count can be calculated.

The curves represent the same general planning relationship across assumed effect sizes: the participant requirement increases as the target effect becomes smaller. The calculations are illustrations based on observed results and stated assumptions, not observed power for this completed trial. They do not establish that the original study was adequately sized, because the original design rationale is 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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.310; pooled standard deviation σ = 2.331.
2. n = 2 × (1.96 + 0.842)² × 2.331² / 0.310² = 887.6, rounded up to 888 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 <- 0.31                      # observed difference in means
sigma <- 2.33100836549335                     # 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(6815562)
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 = 888 (80% power), 1,189 (90% power)
 75% of observed effect: n per arm = 1,578 (80% power), 2,113 (90% power)
 50% of observed effect: n per arm = 3,551 (80% power), 4,753 (90% power)
power.t.test: 888.5 
Simulated power at n = 888 per arm: 0.801 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record does not report how multiplicity was handled across the primary and secondary outcomes, or across the separate child and adolescent results. It does not state whether one outcome was designated as the sole confirmatory test, whether any hierarchy was used, or whether p-values were adjusted for multiple comparisons. The reported p-values are described as unadjusted. When several outcomes or subgroup comparisons are examined, unadjusted results can overstate the strength of evidence if they are interpreted as though only one test had been planned.

Missing-data methods are not reported in the registry record. The number of participants with a reported value differs by arm and outcome, but the record does not explain whether this reflects missing follow-up, exclusions, unavailable ratings, or another reason. It also does not state how missing values were handled, whether the analysis used all randomized participants, or whether complete-case analyses were used. No imputation method or sensitivity analysis is reported.

The analysis populations are not reported in the registry record. In particular, there is no stated intention-to-treat definition, per-protocol population, or description of how participants were analyzed if they did not receive or use the assigned condition. The randomization procedure and allocation concealment are also not described. Since masking was listed as none, the record does not establish whether outcome raters were masked.

Interim analyses, stopping rules, and any data-monitoring procedures are not reported in the registry record. The statistical model, covariate adjustment, assumptions, and confidence level are also not described. These omissions do not prove that such methods were absent from the full study conduct; they mean the registry record does not allow readers to assess them. A complete protocol and statistical analysis plan would be needed to determine whether the reported results follow the originally intended analyses.

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 affecting participants in each listed arm and zero other adverse events affecting participants in each listed arm. Deaths are also recorded as zero across the child and adolescent experimental and control groups. The at-risk counts are listed separately by group for serious and other adverse events.

These entries indicate that no affected participants or deaths were reported in the registry’s safety summary. They should not be interpreted as proof that no adverse experiences occurred. The registry record does not describe how adverse events were defined, the collection period, the method of ascertainment, or whether events were actively solicited. It also does not provide event narratives or a separate account of the seriousness criteria used.

Safety counts describe what was recorded, not the likelihood of an event in every setting or for every youth. The study evaluates access to a decision support tool, and the posted safety information does not establish the safety of any particular placement or clinical service. Interpretation should remain limited to the registry’s recorded adverse-event summary.

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

The primary outcome results describe average change in TOP-CS scores among the listed groups over the study follow-up. The child arm means are positive, while the adolescent arm means are negative; under the registry’s outcome definition, these directions correspond to average worsening and average improvement, respectively. Those within-group patterns do not by themselves show that PSP access caused a difference. A treatment effect requires a valid comparison between the change in the experimental condition and the change in the appropriate control condition.

The child comparison estimate is imprecise, and its interval includes zero. The posted adolescent comparison is not aligned with the adolescent control arm because it uses the child control mean as its comparison input. Therefore the record does not offer a clean, precise primary comparison across both age samples. The results do not establish that access to PSP improved outcomes, nor do they establish that it had no effect. Absence of a clear contrast is not proof of equivalence.

The trial is about access to placement-specific predictions, not assignment to a specific level of care. The record does not report how clinicians used PSP scores, whether placement choices changed, or whether predictions were accurate for individual youth. An observed score difference would not by itself show that the model’s predictions were correct or that a particular placement was beneficial.

These findings should also not be generalized automatically to all clinical settings or youth populations. The registry does not report site count, site characteristics, detailed eligibility criteria, or how the model was customized at each site. The primary outcome is a risk-adjusted symptom measure collected over a defined follow-up period, and it does not capture every aspect of behavioral health or longer-term outcomes.

The proper conclusion is limited: the registry records an unmasked randomized study and posts group summaries, but the primary comparisons offer limited and partly misaligned evidence about the stated hypothesis. The record’s omissions about analysis methods, missing data, multiplicity, and outcome rating further constrain interpretation. This is a statistical reading of the posted record, not a recommendation about care or use of the tool.

17. Why This Trial Matters Statistically

This study raises a consequential statistical question: whether predictions from a site-customized machine learning tool can improve decisions about placement for young people with behavioral health needs. The trial structure is relevant because it compares access to the tool with no access under randomized allocation. The primary outcome also focuses on change over follow-up rather than relying only on a single post-intervention measurement.

At the same time, evaluating decision support requires more than showing that a model can generate predictions. The clinical question concerns what happens when teams receive those predictions. That requires a well-defined treatment contrast, a clearly reported analysis, and measures that connect decisions to youth outcomes. The registry record does not describe clinicians’ use of scores, the resulting placement decisions, or the model’s predictive performance. Those details are important for distinguishing the impact of the tool from the accuracy of its underlying predictions.

The separate child and adolescent reporting recognizes that different age-appropriate TOP-CS instruments are used. But subgroup estimates need careful specification, and the posted adolescent primary comparison does not use the adolescent control mean. This illustrates why a plausible-looking point estimate or p-value cannot replace checking which groups and outcomes were actually compared.

More broadly, the record shows why precision, transparency, and a prespecified statistical plan matter in randomized evaluations. Readers need aligned group comparisons, clear missing-data methods, and an account of multiplicity to assess whether the result answers the stated clinical question. The posted results are informative as a record of group outcomes, but the gaps in analysis reporting limit how firmly they can guide conclusions about the tool’s effects.

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 registry record has several limitations specific to this study. It does not report the site count or describe how site-specific models were developed, validated, or updated. Because PSP is described as site-customized, the absence of those details makes it difficult to assess how comparable the tool was across settings or whether the reported results reflect a common intervention.

The design is unmasked. The record does not state whether outcome raters were masked, how clinical teams used the scores, whether teams followed the predictions, or whether placement decisions differed between conditions. These omissions make it difficult to understand the pathway by which tool access could affect the measured outcome.

The arm-level results have different participant counts by outcome, but reasons for those differences and methods for missing data are not reported. The registry also does not describe the analysis populations, covariate adjustments, or original sample-size rationale. As a result, the reader cannot determine from the record whether the posted summaries reflect the planned analysis or how sensitive they are to incomplete follow-up.

There is a specific alignment concern in the posted comparisons: adolescent comparison inputs use the child control mean rather than the adolescent control mean, for both the primary and secondary summaries. This prevents those posted adolescent contrasts from serving as straightforward experimental-versus-control estimates within the adolescent sample. In addition, the confidence level and detailed statistical methods for the posted intervals are not reported.

Finally, the available outcome is a TOP-CS score over approximately 60-120 days. The registry does not report longer follow-up results or other outcomes that could clarify broader or sustained effects. These limitations do not establish that the study was conducted incorrectly, but they constrain what can be concluded from the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Predict the Best Level of Care Placement for Each Child's Behavioral Health Needs - Efficacy Study — NCT06815562.
• Registry record last updated 2026-07-08; status last verified 2026-06.
• Results first posted 2026-07-08.
• 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

NCT06815562 is a completed, randomized, unmasked, parallel efficacy study sponsored by Outcome Referrals, Inc. The registry records enrollment of 213, a start date of 2025-02-03, and primary completion on 2026-01-26. The study compared clinical team access to Placement Success Predictor site-specific scores with no access, reporting child and adolescent samples separately.

The primary outcome is change in average TOP-CS domain z-scores from baseline to follow-up, with negative within-person differences indicating reduced symptom severity. Child and adolescent arm summaries are posted, but the child comparison interval includes zero and the adolescent comparison uses the child control mean rather than the adolescent control mean. No sponsor-reported analyses are listed. The record also does not report the original sample-size rationale, analysis populations, missing-data methods, or multiplicity handling. Its adverse-event summary records no affected participants or deaths in the listed groups.