Problem-Solving Skills Training to Improve Care for Children With Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Problem-Solving Skills Training to Improve Care for Children With Asthma (NCT00250588), a randomized na study. The primary outcome is Parent Proxy-Reported Health-related Quality of Life (Pediatric Quality of Life Inventory).

2. Clinical Question

The registry describes a study of whether problem-solving skills training could reduce barriers to health care and improve health-related quality of life for children with persistent asthma. Care coordination was included both as a stand-alone intervention and together with problem-solving training. This arrangement makes it possible to consider the combined intervention against standard care, as well as care coordination alone against standard care; it does not, by itself, establish the separate contribution of each component.

The primary measure is a parent proxy report. The record says child self-report was also measured, but identifies the parent proxy report as the a priori primary outcome. The posted primary outcome means are 81.2 for care coordination, 85.4 for care coordination plus problem-solving, and 80.8 for standard care. The registry also posts adjusted mixed-model contrasts, which differ from the unadjusted recalculations. Because the record flags that discrepancy, interpretation of the comparison should give precedence to the sponsor's reported analysis.

3. Trial Design

The registry record describes a randomized, parallel-group trial with no masking. The intervention arms were care coordination and care coordination plus problem-solving skills training; standard care was the control. Enrollment was 252. The study is marked completed, with a start date of 2003-10 and primary completion at 2007-10. Its phase is listed as not applicable.

The interventions are behavioral: problem-solving skills training and asthma care coordination. The combined arm received both interventions, the care coordination arm received care coordination alone, and the control arm received usual care. The registry's arm description calls the control a wait-list control. The record does not report further details about how randomization was generated or concealed, the setting, eligibility criteria, intervention dose, adherence, or allocation procedures.

The primary outcome was parent proxy-reported health-related quality of life on the PedsQL 4.0 Generic Core Scales Total Scale Score. The outcome timeframe lists baseline (T1), post intervention (3mo, T2), and 6-month follow up (9mo post baseline, T3). The record says analyses followed an intent-to-treat approach and a pre-established plan using SAS 9.1.3, with all subjects who had data at T2 or T3 included. It does not report the original sample-size justification, the trial's detailed statistical analysis plan, or whether interim analyses were conducted.

The record lists two secondary outcomes: counts of participants with one or more asthma-related emergency department visits and asthma symptoms. Both are described over the same baseline, post-intervention, and follow-up timeframe. Outcome-specific results and adjusted analyses are not uniformly available across these endpoints. The posted results therefore support a focused reading of the stated primary measure and the reported secondary comparisons, rather than a complete reconstruction of every planned analysis.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All analyses were intent-to-treat and carried out according to a pre-established plan using SAS 9.1.3. All subjects with data at T2 or T3 were included in the analyses.

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 Parent Proxy-Reported Health-related Quality of Life (Pediatric Quality of Life Inventory), measured over Baseline (T1), Post Intervention (3mo, T2), 6-month follow up (9mo post baseline, T3).

The primary endpoint is parent proxy-reported health-related quality of life measured with the PedsQL 4.0 Generic Core Scales Total Scale Score. The instrument contains 23 items asking how often different issues have been a problem during the past month. Its score ranges from 0 to 100, with higher scores indicating better reported quality of life. The registry describes the instrument as internally consistent, valid, and responsive to indicators of clinical change for children with asthma.

Parents completed the proxy form for children in the age range described by the record, while a parallel child self-report form was available for children ages 5-18 years. The study measured both forms, but the registry identifies parent proxy report as the a priori primary outcome. The record does not post the child self-report results in the analyses, so those results cannot be used to assess whether child and parent reports agreed.

Health-related quality of life is relevant to a study aimed at reducing barriers to care because it captures reported effects on a child's day-to-day well-being, rather than only counting service use or symptoms. It is a continuous score, so group means and mean differences are used to describe average scores. That summary does not show the full distribution of individual scores or how many children experienced a particular amount of change. The outcome timeframe includes baseline, post intervention, and follow-up assessments; the arm summary values alone do not identify a specific assessment time in the posted results.

7. Results Posted in the Registry

• Care Coordination: mean 81.20 versus 80.80 on control; difference 0.40 (95% CI -3.62 to 4.42), standardized effect d = 0.03; z-test p = 0.845.
• Care Coordination+Problem Solving: mean 85.40 versus 80.80 on control; difference 4.60 (95% CI 0.44 to 8.76), standardized effect d = 0.37; z-test p = 0.030.

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.

Counts of Patients With One or More Asthma-related Emergency Department Visits.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Care Coordination: 13.9% (10/72) versus 13.5% (10/74) on control; risk difference 0.4 percentage points (95% CI -10.8 to 11.5), risk ratio 1.03 (0.46–2.32); unadjusted two-proportion z-test p = 0.947.
  • Care Coordination+Problem Solving: 6.2% (4/65) versus 13.5% (10/74) on control; risk difference -7.4 percentage points (95% CI -17.1 to 2.4), risk ratio 0.46 (0.15–1.38); unadjusted two-proportion z-test p = 0.150.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Care Coordination and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Care Coordination+Problem Solving and the control. The interval gives the range of effects that remain compatible with the data.

Asthma Symptoms

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Care Coordination: 29.2% (21/72) versus 32.4% (24/74) on control; risk difference -3.3 percentage points (95% CI -18.2 to 11.7), risk ratio 0.90 (0.55–1.46); unadjusted two-proportion z-test p = 0.669.
  • Care Coordination+Problem Solving: 13.8% (9/65) versus 32.4% (24/74) on control; risk difference -18.6 percentage points (95% CI -32.2 to -5.0), risk ratio 0.43 (0.21–0.85); unadjusted two-proportion z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Care Coordination 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 proportion with the event is statistically lower for Care Coordination+Problem Solving than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists two secondary outcomes, one concerning asthma-related emergency department visits and the other concerning asthma symptoms. Across these outcomes, the combined care coordination and problem-solving arm has sponsor-reported results that point in a favorable direction relative to standard care, while the reported emergency department comparison is more uncertain. The stand-alone care coordination comparisons do not show the same consistent pattern across the posted analyses. This broad pattern is not identical to the primary endpoint pattern, and secondary outcomes should not be treated as confirmation of the primary result.

Secondary endpoints can provide useful context because they address aspects of asthma-related experience and service use that differ from parent-reported quality of life. However, they may have distinct definitions, measurement properties, and sources of missingness. The registry record does not provide enough detail to establish whether outcomes were assessed at a single common time point for these comparisons or how all repeated assessments were incorporated into the sponsor's models.

Unadjusted secondary results carry less weight when several outcomes and comparisons are examined without a reported multiplicity procedure. With multiple opportunities to observe an apparently unusual result, some findings can arise by chance even if there is no underlying difference. The record does not report whether the secondary analyses were prespecified in a formal analysis plan, prioritized, or adjusted for multiplicity. Their role is therefore best understood as complementary evidence that merits cautious interpretation, not as independent proof of benefit or as a replacement for the prespecified primary outcome.

The primary and secondary measures also operate on different scales: the primary is a continuous quality-of-life score, while the listed secondary outcomes are participant counts with binary comparisons. Agreement across these outcomes would not automatically establish a single common effect, and disagreement would not by itself invalidate any one measure. Clinical interpretation requires attention to each outcome's definition, the analysis used, precision, missing data, and the importance of the measured difference.

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

• Counts of Patients With One or More Asthma-related Emergency Department Visits.
• Asthma Symptoms

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a score on a scale, summarized by a mean and standard error for each arm. A mean describes the group's average score, while a standard error describes the estimated precision of that mean. The posted arm means are 81.2 for care coordination, 85.4 for care coordination plus problem-solving, and 80.8 for standard care. Standard errors are reported as 1.4, 1.5, and 1.5, respectively. A standard error is not the same as the spread of individual participant scores; the registry does not give arm-level standard deviations for this endpoint.

For a two-group comparison of a continuous outcome, a mean difference expresses how far apart the group averages are, with the direction depending on which group is subtracted from which. The unadjusted recalculation compares each intervention arm with standard care using the posted summary statistics. The recalculated mean difference for the combined intervention is 4.6, while the difference for care coordination alone is 0.4. These are not the sponsor's adjusted results. A recalculation based on group summaries generally cannot reproduce a model that accounts for repeated measurements or other model terms, and the registry does not provide enough detail to identify the reason for the discrepancies.

The sponsor reports mixed-model analyses for the primary endpoint. In general, a mixed model can account for dependence among repeated measurements from the same participant and can estimate contrasts while using information across assessment times. That is a general description of the method, not a claim about the exact model specification used in this trial. The registry record does not report the model's fixed or random effects, covariance structure, covariates, handling of missing observations, or the exact contrast coding. It reports that analyses followed an intent-to-treat approach and a pre-established plan using SAS 9.1.3, and that all subjects with data at T2 or T3 were included.

A confidence interval gives a range of values compatible with the observed data under the assumptions of the analysis. It communicates uncertainty around an estimate, rather than giving the probability that the true effect lies in the particular interval. For the sponsor's combined-intervention contrast, the reported 95% confidence interval is 0.63 to 7.4. For care coordination alone, it is -0.21 to 6.4. A 95% interval is often used to describe the long-run performance of the interval procedure under repeated sampling; it is not a guarantee about any single result. The interval's width conveys precision: narrower intervals indicate more precise estimates, all else equal.

The unadjusted p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. It does not measure the probability that the null hypothesis is true, the size of an effect, or whether an effect matters to families. The sponsor reports p = 0.05 for each primary mixed-model comparison. The recalculated unadjusted p-values differ: p = 0.03 for the combined intervention and p = 0.845 for care coordination alone. Because the recalculations and sponsor analyses are not the same analysis, the p-values should not be treated as interchangeable.

The secondary binary outcomes are summarized as counts and compared using risk differences in the unadjusted recalculations. A risk difference is the difference between the proportions with the outcome in two groups. The sponsor's posted analyses use logistic regression and report odds ratios. An odds ratio compares the odds of an outcome between groups; it is not the same quantity as a risk difference. Both can describe a contrast, but their scales and interpretations differ. The registry record does not specify the complete regression models or whether covariates were included.

General statistical context: binary outcomes can be sparse, particularly when relatively few participants experience the event. In that setting, estimates may be imprecise, and confidence intervals can be wide. The emergency department comparison has a sponsor-reported odds ratio of 0.49 with a 95% confidence interval from 0.18 to 1.38, illustrating uncertainty across a range of possible association sizes. The asthma-symptom contrast has an odds ratio of 0.33 with a 95% confidence interval from 0.13 to 0.82. Neither interval alone resolves issues such as multiplicity, outcome definition, missingness, or whether the estimate is clinically meaningful.

General statistical context: multiplicity arises when several outcomes, groups, time points, or comparisons are assessed. Each additional test can increase the chance that at least one result appears unusual by chance if no adjustment or prespecified prioritization is used. The record identifies a primary outcome and lists secondary outcomes, but does not report a multiplicity procedure. The primary outcome should therefore remain the main focus, while secondary findings should be interpreted as supportive or exploratory unless the analysis plan establishes otherwise.

General statistical context: over-dispersion matters for count outcomes when observed variability exceeds what a simple count model expects. The posted secondary outcomes are represented as binary participant counts, not as event-rate counts, and the registry does not report an over-dispersion assessment or a count-model analysis. It would therefore be inappropriate to infer that a particular over-dispersion adjustment was used.

The study's original design assumptions, including its sample-size justification and planned target power, are not reported in the registry record. The separate planning illustrations use the observed effect as a starting point under stated assumptions; they are not evidence about the original design or the trial's achieved power. The registry also does not report interim analyses, a detailed missing-data method, or a protocol-level account of deviations from the planned analysis.

11. Confidence Intervals and Precision

Precision is best judged from the confidence interval alongside the point estimate. For the sponsor's mixed-model primary comparison of care coordination plus problem-solving with standard care, the estimated net mean difference is 4.0 and the 95% confidence interval runs from 0.63 to 7.4. This interval is consistent with a range of positive differences, but it does not establish how important those differences are to children or families. The record does not identify a minimal clinically important difference for the PedsQL score.

For care coordination alone versus standard care, the sponsor reports a net mean difference of 3.1, with a 95% confidence interval from -0.21 to 6.4. This interval includes zero and spans values on either side of zero, so it does not precisely distinguish a positive difference from little or no difference. The p-value is reported as 0.05, but the interval gives more information about the range of effect sizes compatible with the analysis than that threshold alone.

The recalculated intervals differ from the sponsor's intervals. For the combined intervention, the unadjusted interval is 0.442 to 8.758; for care coordination alone, it is -3.622 to 4.422. Because the registry flags a discrepancy, the sponsor's own analysis takes precedence. The recalculations remain useful as a check on the posted summaries, but should not be substituted for the sponsor's model-based estimates.

For the secondary outcomes, the emergency department odds-ratio interval is 0.18 to 1.38, while the asthma-symptom interval is 0.13 to 0.82 for the sponsor-reported combined-intervention comparisons. Intervals that include the null value of 1 for an odds ratio do not clearly separate the data from no association under that model; intervals excluding 1 indicate a more restricted range, but do not address clinical importance or multiplicity. The registry's missing details about model specification, missing observations, and multiplicity limit how far precision can be interpreted.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial's original design assumptions. For these comparisons, the figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The original trial's sample-size justification and design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column uses a higher probability of detection and therefore generally calls for more participants per arm for the same effect. These are planning targets, not a description of what happened in the completed trial.

Rows labeled as planning for 100%, 75%, and 50% of the observed effect illustrate how the target effect size changes the calculated sample size. Smaller effects are harder to distinguish from random variation and need more participants. This is particularly important where the observed effect is small or uncertain: extrapolating a planning calculation from an observed estimate does not guarantee that the same effect would recur in another study.

The sample-size illustrations are not observed power. They do not establish whether the trial was adequately powered at its start, nor do they change the uncertainty in the posted estimates. Their role is prospective: to show how participant requirements would vary under the stated assumptions and effect scenarios.

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 = 0.400; pooled standard deviation σ = 12.409.
2. n = 2 × (1.96 + 0.842)² × 12.409² / 0.400² = 15,107.7, rounded up to 15,108 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 <- 0.400000000000006                      # observed difference in means
sigma <- 12.4091196303364                     # 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(250588)
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 = 15,108 (80% power), 20,225 (90% power)
 75% of observed effect: n per arm = 26,859 (80% power), 35,956 (90% power)
 50% of observed effect: n per arm = 60,431 (80% power), 80,900 (90% power)
power.t.test: 15108.7 
Simulated power at n = 15,108 per arm: 0.799 (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. Analyses Reported by the Sponsor

The sponsor's primary analyses are mixed-model estimates, while the recalculations are simple, unadjusted comparisons from the posted group summaries. For care coordination plus problem-solving versus standard care, the sponsor reports a net mean difference of 4.0, a 95% confidence interval from 0.63 to 7.4, and p = 0.05. The recalculated comparison is 4.6, with a 95% confidence interval from 0.442 to 8.758 and p = 0.03.

For care coordination alone versus standard care, the sponsor reports a net mean difference of 3.1, a 95% confidence interval from -0.21 to 6.4, and p = 0.05. The recalculation is 0.4, with a 95% confidence interval from -3.622 to 4.422 and p = 0.845. The registry record flags a discrepancy between the posted analyses. Accordingly, the sponsor's own analysis takes precedence; the recalculations should be read as unadjusted checks, not corrections to the model-based results.

The record does not explain the source of the differences or give enough model detail to reproduce the sponsor's estimates. It is not possible to determine from the registry record whether the divergence reflects model structure, repeated-measure handling, adjustment, outcome timing, or another analysis choice. The appropriate reading is to report both sets of figures with their methods distinguished, while basing the primary interpretation on the sponsor's reported analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies parent proxy-reported health-related quality of life as the a priori primary outcome and lists two secondary outcomes. It does not report a multiplicity adjustment, a hierarchy for testing the secondary outcomes, or a complete account of the number of hypotheses tested across all measures and time points. Without that information, unadjusted p-values for secondary analyses should be treated cautiously. A nominally small p-value does not account for the broader set of comparisons that may have been considered.

The record describes the analyses as intent-to-treat and says all subjects with data at T2 or T3 were included. These statements indicate an intention to analyze participants according to their assigned groups, while also making observed data at the follow-up assessments a condition for inclusion in the analyses described. The registry does not report how many participants lacked data at each time point, reasons for missingness, or the precise method used to handle missing outcomes. It also does not describe sensitivity analyses for different assumptions about missing data.

Missing data can affect interpretation if the availability of an outcome is related to a participant's health, intervention experience, or other factors. General statistical context: methods that use available repeated observations can make efficient use of observed data, but their validity depends on assumptions about why data are missing and on correct model specification. The registry record does not report enough information to assess those assumptions or determine whether missingness differed by arm.

The record says an analysis plan was established in advance and that SAS 9.1.3 was used, but the plan itself and its details are not reported in the registry record. Interim analyses, stopping rules, adjustments for multiple outcomes, treatment of protocol deviations, and the exact analysis populations beyond the stated T2 or T3 data criterion are also not reported in the registry record. These omissions do not demonstrate that procedures were absent; they limit what can be verified from the registry information.

16. 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 serious adverse event figures report zero affected participants in each arm: care coordination, care coordination plus problem-solving, and standard care. The corresponding numbers at risk are 81, 84, and 87. The record also reports zero participants with other adverse events in each of those groups, using the same numbers at risk.

These figures describe what is posted in the registry record; they do not establish that no adverse events occurred outside the recorded definitions or observation period. The record does not provide serious adverse event terms, and no serious-event terms are listed. Death counts are not reported in the registry record, so they should not be interpreted as zero. The adverse-event denominators also differ from the primary outcome arm sample sizes, and the registry does not explain the reason for those denominators.

Safety figures should be read in the context of the event definitions, follow-up duration, ascertainment procedures, and completeness of reporting. Those details are not reported in the registry record. With zero affected participants recorded in each group, the listed counts alone cannot establish equivalence in safety between groups or rule out events that were not captured in the posted data.

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

The results describe differences and uncertainty in parent proxy-reported quality-of-life scores and in the posted secondary outcomes for the randomized groups. The sponsor's mixed-model primary analysis reports a net mean difference of 4.0 for care coordination plus problem-solving compared with standard care, and 3.1 for care coordination alone compared with standard care. The intervals and p-values indicate that these estimates have uncertainty; they do not establish how meaningful the differences are to children and families.

The registry record does not state a threshold for a clinically important PedsQL difference. Statistical evidence and clinical importance are different questions: a measured difference may be estimated with varying precision, while its relevance depends on whether the size and nature of that difference matter to participants. The posted results do not provide enough information to answer that question definitively.

The record also does not allow a firm conclusion about which element of the combined intervention accounts for any observed difference. The intervention arms compare packages that differ in more than one component, and the available contrasts are against standard care rather than a reported factorial analysis that isolates component effects. Nor do the results establish that the findings apply to children beyond the population enrolled in this study.

The secondary results provide additional outcome-specific information, but they involve unadjusted comparisons and the record does not report multiplicity handling. Differences between these outcomes and the primary result are not necessarily contradictory because they measure distinct aspects of asthma-related experience. Similarly, the absence of recorded adverse events in the posted figures is not proof that risk is absent.

The most defensible conclusion is descriptive: the registry reports particular model-based estimates, confidence intervals, and secondary analyses, with important gaps in model detail, missing-data reporting, and clinical-importance criteria. These results should not be translated into medical advice or a claim that an intervention works or does not work.

18. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation depends on more than a point estimate or a threshold p-value. For the primary outcome, the sponsor's mixed-model results and simple recalculations are not the same. The record flags a discrepancy, so the model-based sponsor analyses take precedence, while the recalculations show how direct comparisons of posted summaries can differ from an analysis that uses a statistical model.

It also demonstrates the value of confidence intervals. A mean difference alone does not reveal how uncertain the estimate is. The sponsor's intervals show different degrees of compatibility with zero for the two primary contrasts, and the secondary odds-ratio intervals likewise communicate uncertainty beyond the point estimates. This helps readers distinguish a direction of estimate from the precision and range of values consistent with the analysis.

The trial also raises familiar issues in outcome reporting. A continuous quality-of-life endpoint, participant counts for secondary outcomes, and adverse-event counts each describe different quantities. Their results should not be combined into a single claim without considering how they were measured and analyzed. The record's limited reporting on model specification, missing data, and multiplicity constrains a full audit of the results.

Finally, the planning illustrations clarify the relationship between target effect size and sample requirements under stated assumptions. They are not a substitute for the original design justification and are not observed power. Keeping planning calculations, sponsor analyses, and simple recalculations distinct is essential for transparent statistical communication.

19. 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 leaves important details unreported. It does not give the original sample-size justification or the trial's own design assumptions, detailed randomization and concealment procedures, eligibility criteria, setting, intervention dose, adherence, or masking beyond the designation of no masking. The reason the adverse-event denominators differ from the primary outcome arm sizes is also not reported in the registry record.

For the primary endpoint, the record does not identify which assessment time corresponds to the posted arm means. It describes measurements at baseline, post intervention, and follow-up, but the summary values do not specify a time point. The sponsor's mixed-model specification is not reported in sufficient detail to reproduce the estimates, and the registry does not explain the discrepancy between those results and the unadjusted recalculations.

The record reports that participants with data at T2 or T3 were included, but does not give missing-data counts by arm or time, reasons for missingness, or sensitivity analyses. Child self-report was measured, but results are not included in the posted analyses. A clinical-importance threshold for the PedsQL score is also not reported in the registry record.

Multiplicity handling is not reported, making unadjusted secondary findings less conclusive. The secondary outcomes are posted as counts, while the sponsor's analyses use logistic regression; model details and any covariate adjustment are not given. Safety reporting is limited to the posted counts, with no listed serious-event terms and deaths not reported. These limitations restrict reproducibility and the scope of conclusions that can be drawn from the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Problem-Solving Skills Training to Improve Care for Children With Asthma — NCT00250588.
• Registry record last updated 2013-06-03; status last verified 2013-04.
• Results first posted 2013-06-03.
• 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.

23. Record Summary

The registry record describes a completed, randomized, parallel-group study with no masking and enrollment of 252 participants. It compared asthma care coordination, care coordination plus problem-solving skills training, and standard care for children with asthma. The primary outcome was parent proxy-reported health-related quality of life measured with the PedsQL 4.0 Generic Core Scales Total Scale Score.

The sponsor reports mixed-model net mean differences of 4.0 for the combined intervention versus standard care and 3.1 for care coordination alone versus standard care. The registry flags a discrepancy between these results and unadjusted recalculations, so the sponsor's analysis takes precedence. Secondary outcomes include asthma-related emergency department visits and asthma symptoms. Serious adverse events and other adverse events are posted as zero in each arm; deaths are not reported in the registry record.

Important details about the original sample-size justification, model specification, multiplicity, and missing-data handling are not reported in the registry record. The results therefore support cautious interpretation of the posted estimates rather than a definitive claim about clinical importance or effectiveness.