Early Intervention for Children at Risk for Anxiety: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Early Intervention for Children at Risk for Anxiety (NCT00865306), a randomized na study. The primary outcome is Number of Responders Based on Clinician Global Impression-Anxiety Improvement.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group trial with single masking, sponsored by Massachusetts General Hospital. The registry lists an enrollment of 65. It describes an earlier open pilot in 9 children and then a randomized comparison of the intervention with a monitoring-only wait-list control. The trial status is completed. The registry gives a start date of 1998-03 and a primary completion date of 2005-01.

Children were blocked according to whether a parent had an anxiety disorder and then assigned to intervention or wait-list control. The eligibility description included children with an anxiety disorder, behavioral inhibition, or elevated anxiety symptoms alongside a parent’s anxiety disorder. The registry summary notes that all but one child had at least one anxiety disorder at baseline, so the enrolled group was largely made up of children with an established anxiety disorder rather than only children considered at risk.

The intervention is described as a 20-session program in the study summary. That summary specifies 6 parent-only sessions, 8–13 child-parent sessions, and a final parent session. The arm description instead lists 7 parent-only and 8–13 child-only sessions. The registry does not resolve this difference in the descriptions. The control group received no intervention.

Assessments were planned at post-trial, described as six months from baseline, and at one-year follow-up. The primary endpoint concerns the post-treatment assessment. The randomized trial arm counts shown for that endpoint are 34 for active CBT and 30 for wait-list control; the registry does not explain the relationship between these counts and the enrollment of 65. Details of concealment, additional follow-up results, the original sample-size rationale, and the trial’s full statistical analysis plan are not reported 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.

Before assignment: We screened 103 children for the controlled trial, to enroll our target goal of 60-65 children. Of these 14 were ineligible (3 did not meet inclusion criteria, and 9 met exclusion criteria). Another 13 withdrew prior to completing baseline assessments, and 11 who did not complete baseline assessments were lost to follow-up. Thus 65 were enrolled.

Controlled Trial

Reasons for not completing this period:

One-Year Follow-Up

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Responders Based on Clinician Global Impression-Anxiety Improvement, measured over Post-Treatment (6-months from baseline).

The primary endpoint counts participants classified as responders using the Clinician Global Impression-Anxiety Improvement scale. Clinicians who were blind to treatment assignment rated each child’s overall improvement in anxiety. The scale ranges from a best value of 1 to a worst value of 7. A responder was defined as a child with a score of 1 or 2, corresponding to “very much” or “much” improvement.

This is a binary endpoint: each participant is counted as a responder or not a responder. Such an endpoint can make a clinical rating easier to summarize as a group count, but it compresses the scale’s range. It does not retain distinctions between children rated 1 and 2, or among children who did not meet the responder threshold. The posted endpoint therefore addresses how many children crossed the specified improvement threshold, not the full distribution of clinician ratings or changes in symptoms on another measure.

Clinician ratings were made by assessors described as blind to assignment. Blinding can reduce the possibility that knowledge of group assignment influences outcome assessment, although the registry record does not give further details about how blinding was maintained. The endpoint was assessed at post-treatment, six months from baseline. The result should be interpreted as a comparison at that specified assessment, not as a summary of the one-year follow-up, for which results are not reported in the registry record.

7. Results Posted in the Registry

• Active CBT: 58.8% (20/34) versus 30.0% (9/30) on control; risk difference 28.8 percentage points (95% CI 5.5 to 52.1), risk ratio 1.96 (1.06–3.63); unadjusted two-proportion z-test p = 0.021.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary because participants are counted as either responders or nonresponders. For a binary outcome, a group’s response proportion is the number of responders divided by the number assessed in that group. Comparisons can then be expressed on different scales. The risk difference compares the proportions by subtraction; the risk ratio compares them by division; and the odds ratio compares the odds of response. Each scale answers a related but distinct question. Absolute differences describe changes in proportions, while ratios describe relative contrasts.

What does the chi-squared test assess?

The registry reports a chi-squared analysis for the two groups, with p < 0.05. In general, a chi-squared test assesses whether the observed distribution of a categorical outcome across groups is compatible with a null hypothesis of no association between group and outcome. For this endpoint, the categories are responder and nonresponder, and the groups are active CBT and wait-list control. The test’s p-value describes how compatible the observed data are with that null model, under the assumptions of the test. It does not measure the size or importance of the difference, and it is not the probability that the null hypothesis is true.

The registry does not report the sponsor’s test statistic or a precise sponsor p-value; it reports only p < 0.05. A separate unadjusted recalculation from the posted summary counts gives p = 0.021. Since a discrepancy is flagged, the sponsor’s own analysis takes precedence over the recalculation. The recalculation is useful as a transparent check based on the displayed counts, but it should not be mistaken for the sponsor’s complete analysis or treated as a replacement for it.

How should effect measures be read?

The recalculated risk difference describes the absolute contrast between the observed response proportions. Its confidence interval is entirely above zero, indicating that the recalculated interval does not include the no-difference value for that scale. The recalculated risk ratio is 1.961, and its 95% confidence interval is 1.06 to 3.626. The recalculated odds ratio is 3.333, and its 95% confidence interval is 1.181 to 9.406. For ratio measures, a value of 1 represents no relative difference. These measures are unadjusted and based on the posted counts; they do not incorporate additional covariates or account for any unreported analysis choices.

Risk ratios and odds ratios are not interchangeable. A risk ratio compares probabilities, while an odds ratio compares odds. When outcomes are common, an odds ratio can be farther from 1 than the corresponding risk ratio. Neither measure alone conveys the precision or the absolute number of responders, so the arm counts remain important context. The confidence intervals add information about uncertainty around the recalculated estimates.

Why does the analysis choice matter?

Statistical results can depend on the analysis specification, including the test, adjustments, analysis population, treatment of missing outcomes, and any stratification or blocking factors. The trial was blocked on parental anxiety disorder, but the registry does not report whether or how the sponsor’s primary analysis accounted for that blocking. It also does not give enough detail to reconstruct the sponsor’s calculation. The recalculated analysis is explicitly a simple, unadjusted calculation from summary statistics. It cannot reveal whether a difference from the sponsor result reflects adjustment, a different analysis population, a different method, or another choice. The cause of the discrepancy is not reported in the registry record.

In general, a p-value addresses evidence against a particular null model, whereas an effect estimate describes the direction and scale of a contrast. A confidence interval conveys a range of estimates compatible with the data and the method used, subject to the model’s assumptions. These summaries are complementary. A result with a small p-value may still have substantial uncertainty about the size of the effect, and a confidence interval should not be treated as a guarantee that the true value lies within its endpoints.

For this trial, the sponsor reports a chi-squared result at the threshold p < 0.05, while the posted summary counts support an unadjusted recalculation. The discrepancy means readers should distinguish clearly between the sponsor’s analysis and the recalculated measures. The available record does not provide enough detail to reproduce the sponsor’s result or adjudicate why the analyses differ.

10. Confidence Intervals and Precision

The recalculated risk-ratio estimate is 1.961, with a 95% confidence interval from 1.06 to 3.626. The recalculated odds-ratio estimate is 3.333, with a 95% confidence interval from 1.181 to 9.406. These intervals exclude 1, the no-relative-difference value for ratio measures, but span a range of possible relative effect sizes. In particular, the odds-ratio interval is broad. The interval for the recalculated risk difference is entirely above zero, although its endpoints are not stated because the posted values have more than three decimal places.

In general, a confidence interval is a measure of statistical precision under the method used. A wider interval indicates greater uncertainty about the effect estimate; a narrower interval indicates greater precision. The interval does not represent a range containing every plausible explanation, and it does not account for sources of bias or incomplete reporting that are not included in the calculation. These recalculated intervals use the posted group counts and are unadjusted.

The sponsor’s reported result is a chi-squared test with p < 0.05, not a reported effect estimate with a sponsor confidence interval. Since the record flags a discrepancy, the sponsor’s own analysis takes precedence. The available record does not give the sponsor’s precise effect estimate or confidence interval, so the recalculated intervals should not be presented as though they were sponsor-reported results. Precision is also constrained by the group sizes: the endpoint counts are 34 and 30 participants, and the registry does not clarify how the 65 enrolled participants relate to those counts.

11. 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 figures are planning illustrations based on the observed effect, not the trial’s original design calculation. For this binary endpoint, the figures are participants per arm, not total events. In general, a time-to-event planning display may instead express the required total number of events; that is not the format used for this result.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is expressed as a stated fraction of the observed effect. The trial’s original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect is the true effect and the analysis model applies. The 90% power column gives the corresponding planning target for a 90% chance. These are design calculations, not measures of what the completed trial achieved. This is not observed power.

The rows consider planning for 100%, 75%, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so planning for smaller effects requires more participants per arm. The values are illustrative because the observed effect comes from a relatively small trial and may not be a stable estimate of the effect a future study should target. They do not establish that a future trial will obtain the assumed effect or reach a particular result.

12. 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 = 0.300; treatment proportion p₁ = 0.588; average p̄ = 0.444.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7027 = 1.3772.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6725 = 0.5660.
4. n = (1.3772 + 0.5660)² / (0.2882)² = 45.5, rounded up to 46 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 <- 0.3                          # control proportion
p1 <- 0.588235294117647                          # 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(865306)
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 = 46 (80% power), 61 (90% power)
 75% of observed effect: n per arm = 80 (80% power), 107 (90% power)
 50% of observed effect: n per arm = 176 (80% power), 235 (90% power)
power.prop.test: 45.5 
Simulated power at n = 46 per arm: 0.791 (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.

13. Analyses Reported by the Sponsor

The registry reports that the sponsor’s analysis compared the two groups with a chi-squared test and gives p < 0.05. It does not report a sponsor effect estimate, confidence interval, or exact p-value. The recalculated analysis uses the posted responder counts: 20 of 34 in the active CBT group and 9 of 30 in the wait-list group. From those summary statistics, the unadjusted recalculated p-value is 0.021, with recalculated risk-ratio and odds-ratio estimates and confidence intervals.

The registry flags a discrepancy between the sponsor’s analysis and the recalculation. Accordingly, the sponsor’s own analysis takes precedence. The recalculated statistics are not a correction to the sponsor’s result, nor do the available details establish why the results differ. The record does not specify whether the cause is an adjustment for the blocking factor, a different analysis population, another statistical method, or a different handling of outcome data.

Readers should keep the distinction between the two sources of analysis in view: the sponsor’s reported chi-squared result and the unadjusted check based on posted counts. The record is not detailed enough to reproduce the sponsor’s analysis or explain the discrepancy. The sponsor result is therefore the primary reported inference, while the recalculation gives a separate, limited summary of the counts.

14. Multiplicity, Missing Data and Analysis Populations

The record describes three outcome measures, but it contains no posted secondary outcome results. The primary endpoint is the responder count based on clinician-rated improvement at post-treatment. The registry does not report a multiplicity plan describing whether the primary endpoint was designated as the sole confirmatory outcome, whether other outcomes were tested, or how multiple comparisons were handled. Without that information, the reported p-value cannot be interpreted in the context of a known family of planned statistical tests.

The registry describes assessments at six months and at one-year follow-up, but results for the one-year assessment are not reported in the registry record. It does not give the number of participants assessed at each time point, reasons for missing assessments, or the method used to handle missing outcome data. It is therefore not possible to determine from the record whether the displayed endpoint counts include all randomized participants, only those with available assessments, or another analysis population.

The endpoint arm counts are 34 and 30, while the overall enrollment is 65. The registry does not explain the relationship between those figures. No assumption should be made about whether the difference reflects missing data, exclusion, or another reason. The record also does not report an intention-to-treat definition, a per-protocol definition, or the specific population used in the sponsor’s analysis.

In general, multiplicity matters because testing multiple outcomes or time points can increase the chance of at least one apparently notable result if no adjustment or prespecified hierarchy is used. Missing-data methods matter because the analysis can depend on who has observed outcomes and on assumptions about those without them. These are general statistical considerations; the relevant plans and details for this trial are not reported in the registry record.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

The registry lists 0 serious adverse events among 34 participants at risk in the active CBT group and 0 among 30 participants at risk in the wait-list control group. It also lists 0 other adverse events among the same at-risk group counts. Death counts are not reported in the registry record.

These entries describe the adverse-event figures recorded for the listed groups. They do not establish that no adverse events occurred outside the information captured in the record, and they do not provide detail on event definitions, collection procedures, timing, or severity beyond the serious-versus-other categories. The record does not list serious adverse-event terms.

Zero recorded events in these groups should be read as a description of the registry data, not as proof that the intervention has no risks. The trial’s group sizes and the lack of further safety detail limit what can be concluded about uncommon events. The figures also do not replace a complete account of adverse-event monitoring or follow-up, which is not reported in the registry record.

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

The posted primary outcome counts show that 20 participants in the active CBT arm met the responder definition, compared with 9 participants in the wait-list control arm at post-treatment. The sponsor’s reported chi-squared analysis gives p < 0.05. The recalculation from the posted counts also gives an unadjusted p-value of 0.021, but the registry flags a discrepancy, so the sponsor’s own analysis takes precedence. The sponsor’s precise effect estimate and confidence interval are not reported in the registry record.

This result concerns a specific threshold on a clinician rating scale at one assessment time. It does not describe every child’s rating, the amount of improvement below or above the threshold, or changes at the one-year follow-up. It also does not identify which parts of the multicomponent program are associated with the response counts. Because the comparator received no intervention, the comparison cannot separate the intervention’s specific CBT content from other differences between receiving the program and waiting without intervention.

The finding is from a randomized trial of children at risk for anxiety, most of whom reportedly had an anxiety disorder at baseline. It should not be treated as an estimate for all children, all clinical settings, or all forms of CBT. The registry does not report adherence, missing-data handling, the sponsor’s analysis population, secondary results, or the original sample-size rationale. Those gaps limit interpretation of who is represented by the analyzed counts and how the primary analysis was conducted.

In general, a statistically notable group comparison does not establish an individual outcome or guarantee that a similar result will occur in another study. The counts and estimates describe this trial’s posted data. They do not by themselves establish the persistence of the response, the comparative effects against another active treatment, or the full balance of potential benefits and harms.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it combines a small randomized comparison with a binary clinician-rated endpoint and a sponsor result that cannot be fully reconstructed from the registry record. The displayed responder counts make the comparison understandable, while the reported chi-squared result and the recalculated statistics illustrate why an effect estimate and its precision matter alongside a p-value.

The registry’s discrepancy flag is especially important for interpretation. The unadjusted recalculation from summary counts gives a different analysis basis from any potentially adjusted or otherwise specified sponsor analysis. The record does not explain the difference, and the detailed sponsor estimate is not available. Treating those analyses as interchangeable would obscure the limits of the available information. Giving precedence to the sponsor’s own analysis while labeling the recalculation clearly preserves that distinction.

The trial also highlights the importance of endpoint definition. A responder threshold turns a clinician rating into a count, which is straightforward to interpret, but it discards variation within responder and nonresponder categories. The endpoint therefore answers a focused question about crossing a threshold rather than providing a complete account of clinical change.

Finally, the record illustrates how reporting details affect statistical interpretation. The enrollment figure does not align transparently with the endpoint arm counts, and the registry does not report missing-data methods, analysis populations, or secondary results. These are not reasons to disregard the posted primary result; they are reasons to keep its scope precise and its uncertainty visible.

18. Limitations

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

Several trial-specific details constrain interpretation. The registry reports enrollment of 65, while the primary endpoint counts show 34 participants in the intervention arm and 30 in the wait-list arm. The record does not explain how these numbers relate, so the reasons for the difference cannot be determined. Missing outcome counts and the handling of missing data are not reported.

The intervention descriptions are not fully consistent. The study summary describes 6 parent-only sessions, 8–13 child-parent sessions, and a final parent session, while the arm description gives 7 parent-only and 8–13 child-only sessions. The registry does not resolve the difference. That limits precise reconstruction of the delivered intervention from the record alone.

The study summary says all but one child had at least one anxiety disorder at baseline, although the eligibility criteria also allowed behavioral inhibition or elevated symptoms in the context of a parent’s anxiety disorder. The results therefore should not be generalized automatically to children with risk indicators but no baseline anxiety disorder.

The record describes one-year follow-up assessments but does not report their results. It also does not report secondary outcome results, adherence, the original sample-size assumptions, the sponsor’s precise effect estimate, or enough detail to reproduce the sponsor’s analysis. A discrepancy between the sponsor analysis and recalculation is flagged, but its cause is not reported. These gaps limit assessment of durability, analysis choices, and the relationship between the posted counts and the sponsor’s inference.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Early Intervention for Children at Risk for Anxiety — NCT00865306.
• Registry record last updated 2026-04-24; status last verified 2026-04.
• Results first posted 2010-10-13.
• 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, single-masked, parallel-group trial sponsored by Massachusetts General Hospital. It compared a CBT program for young children at risk for anxiety with a no-intervention wait-list control. Enrollment is listed as 65.

The primary endpoint was the number of children rated as responders on the Clinician Global Impression-Anxiety Improvement scale at post-treatment, six months from baseline. The posted counts are 20 of 34 for active CBT and 9 of 30 for wait-list control. The sponsor reports a chi-squared result of p < 0.05. An unadjusted recalculation from the counts is available, but the registry flags a discrepancy and the sponsor’s analysis takes precedence.

The registry does not report secondary outcome results, one-year follow-up results, missing-data methods, or the original sample-size rationale. It lists no serious or other adverse events in either group; deaths are not reported.