Treatment of Traumatic Brain Injury (TBI)-Related Attention Deficits in Children: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Treatment of Traumatic Brain Injury (TBI)-Related Attention Deficits in Children (NCT02712996), a randomized phase 4 study. The primary outcome is Assessing Severity of Symptoms Associated With Attention-deficit/Hyperactivity Disorder (ADHD) in Children When Using Vyvanse Versus Placebo by Administering the Conners-3 Parent Form.

2. Clinical Question

3. Trial Design

This was a Phase 4, randomized, triple-masked crossover trial sponsored by Vanderbilt University. The registry record lists an enrollment of 20 and a completed status. It gives a start date of 2017-02-06 and a primary completion date of 2019-07-01. The planned comparison was lisdexamfetamine versus placebo in children with traumatic brain injury-related attention deficits.

In a crossover design, participants receive more than one study condition in sequence, so comparisons can potentially use information from the same participant under both conditions. The registry record identifies the model as crossover, but does not report the treatment sequence, period order, washout arrangements, or how period effects were handled. Those details matter because an analysis of crossover data may need to account for within-participant correlation and possible effects of treatment order or time.

The listed treatment descriptions specify a morning capsule for 6 weeks for each condition. The primary outcome timeframe is 12 weeks. The record does not explain how these treatment periods fit together in the protocol, whether there were additional visits or assessments, or whether the timeframe includes any interval between conditions. Those design details are not reported in the registry record.

Primary outcome results list 16 observations in the lisdexamfetamine arm and 17 in the placebo arm. The primary outcome population note says one participant completed the placebo arm but dropped out of the lisdexamfetamine arm due to an adverse event. These arm counts and that note do not establish the complete participant flow or the analysis population. A participant flow diagram, sequence-specific counts, and a detailed account of missing outcome data are not reported in the registry record.

Randomization and triple masking are recorded, but the method used to generate the random sequence, the allocation process, and which roles were masked are not reported in the registry record. It also does not report the trial’s original sample-size justification or a detailed statistical analysis plan. The posted numerical comparisons therefore need to be read alongside the limited design and analysis details available in the 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: Of 20 enrolled participants, 3 never began the trial due to scheduling problems or competing demands.

First Intervention (Study Days 1-42)

Second Intervention (Study Days 43-84)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: One participant completed the placebo arm, but dropped out of Vyvanse arm due to adverse event.

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 Assessing Severity of Symptoms Associated With Attention-deficit/Hyperactivity Disorder (ADHD) in Children When Using Vyvanse Versus Placebo by Administering the Conners-3 Parent Form, measured over 12 weeks.

The primary endpoint was the mean Conners-3 Parent Form inattention score, expressed as a z-score, at the 12-week timeframe. Parents use the form to rate behavior in children aged 6 to 18 years. The instrument contains 45 items rated from 0, not true at all, to 3, very much true. Its overall scale ranges from 0, described as better behavior, to 135, described as worse behavior. The inattention scale, rather than the other content scales, was designated as the primary outcome.

The registry record says scores were converted to z-scores, with M=0 and SD=+/-1. A z-score expresses a value relative to a reference distribution in standard-deviation units, which can make results easier to compare with a standardized scale. The record does not identify the reference population or give a separate explanation of how the conversion was performed.

Parent ratings are used to capture observed behavior outside a single test session. The endpoint therefore reflects parents’ reports of inattention symptoms, not a direct measure of brain injury or a laboratory measure of attention. The record also lists secondary assessments of executive functioning, working memory, concentration, and sustained attention, but those are distinct outcomes and do not replace the prespecified primary measure.

For the posted raw scale, lower scores are described as better behavior. The reported standardized arm means were lower for lisdexamfetamine than placebo, but the treatment comparison remains uncertain because its confidence interval includes zero. Interpretation should also recognize that the record does not report the original analysis method or explain how the crossover structure was incorporated.

7. Results Posted in the Registry

• Lisdexamfetamine (Vyvanse): mean 1.00 versus 1.76 on control; difference -0.76 (95% CI -1.65 to 0.13), standardized effect d = -0.58; z-test p = 0.093.

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.

Assessing Executive Functioning in Children When Using Vyvanse Versus Placebo by Administering the Behavior Rating Inventory of Executive Function (BRIEF) - CHILD SELF REPORT

• 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:
  • Lisdexamfetamine (Vyvanse): mean 0.66 versus 0.59 on control; difference 0.07 (95% CI -0.69 to 0.83), standardized effect d = 0.06; z-test p = 0.856.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lisdexamfetamine (Vyvanse) and the control. The interval gives the range of effects that remain compatible with the data.

Assessing Working Memory and Concentration in Children Using Vyvanse Versus Placebo by Measuring Performance on the Digit Span Subtest of the Wechsler Intelligence Scale for Children - Fifth Edition (WISC-V)

• 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:
  • Lisdexamfetamine (Vyvanse): mean -0.27 versus -0.29 on control; difference 0.02 (95% CI -0.61 to 0.65), standardized effect d = 0.02; z-test p = 0.951.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lisdexamfetamine (Vyvanse) and the control. The interval gives the range of effects that remain compatible with the data.

Assessing Sustained Attention and Response Inhibition in Children Using Vyvanse Versus Placebo by Measuring Reaction Time (RT) Standard Error (SE) on the Conners Continuous Performance Task (CPT-II).

• 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:
  • Vyvanse: mean 0.14 versus 0.57 on control; difference -0.43 (95% CI -1.45 to 0.59), standardized effect d = -0.30; z-test p = 0.411.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vyvanse and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover executive functioning, working memory and concentration, and several measures of sustained attention and response inhibition. Their estimates do not show a uniformly large separation between the treatment conditions: the posted summaries include differences close to zero as well as more separated means. This broad pattern does not provide a clear, consistent secondary signal that independently resolves the uncertainty in the primary comparison.

Secondary measures can help assess whether a primary-outcome pattern is accompanied by related changes in other domains. They are not interchangeable with the parent-rated inattention endpoint: the assessments use different instruments and measure different aspects of behavior or performance. Agreement across outcomes can add context, while disagreement may reflect differing constructs, measurement variability, or chance. The registry record does not report a prespecified interpretation framework for combining these outcomes.

The primary measure remains the main basis for addressing the trial’s central question because it is identified as the primary outcome. Secondary results may be informative, but should not be used selectively to replace an uncertain primary estimate. The record lists 23 outcome measures and does not report whether the investigators adjusted for multiple testing, established a hierarchy, or designated particular secondary outcomes as confirmatory.

In general, testing many outcomes increases the possibility that some comparisons will look notable even when there is no underlying difference. Unadjusted secondary comparisons therefore carry less weight than a prespecified primary analysis. The registry record lists no reported analyses, and its secondary comparisons are summary-based and unadjusted. They should be treated as descriptive evidence rather than as independent confirmation of efficacy or absence of effect.

The posted secondary results also do not compensate for missing crossover-analysis details. The record does not show whether their estimates account for treatment sequence, within-participant pairing, or missing observations. Their overall pattern is best understood as additional but limited context alongside the primary result, rather than as a separate conclusive answer.

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

• Assessing Executive Functioning in Children When Using Vyvanse Versus Placebo by Administering the Behavior Rating Inventory of Executive Function (BRIEF) - CHILD SELF REPORT
• Assessing Working Memory and Concentration in Children Using Vyvanse Versus Placebo by Measuring Performance on the Digit Span Subtest of the Wechsler Intelligence Scale for Children - Fifth Edition (WISC-V)
• Assessing Sustained Attention and Response Inhibition in Children Using Vyvanse Versus Placebo by Measuring Reaction Time (RT) Standard Error (SE) on the Conners Continuous Performance Task (CPT-II).
• Assessing Sustained Attention and Response Inhibition in Children Using Vyvanse Versus Placebo by Measuring RT Inter-Stimulus Interval (ISI) on the Conners Continuous Performance Task (CPT-II).
• Assessing Sustained Attention and Response Inhibition in Children Using Vyvanse Versus Placebo by Measuring Hit Reaction Time (RT) Block Change on the Conners Continuous Performance Task (CPT-II).
• Assessing Sustained Attention and Response Inhibition in Children Using Vyvanse Versus Placebo by Measuring Perseverations on the Conners Continuous Performance Task (CPT-II).

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference represent?

For a continuous outcome, a mean is the average of the recorded scores in an arm. A mean difference compares the two arm averages, with its sign determined by the order of subtraction. In the primary comparison, the difference is expressed as lisdexamfetamine minus placebo, so the negative estimate indicates that the posted mean was lower in the lisdexamfetamine arm. The units are z-score units because the endpoint was reported as a z-score.

A mean difference is a summary of group averages. It does not show the full distribution of individual responses, whether every participant changed in the same direction, or whether any observed difference matters to families. The record does not give a threshold for a clinically meaningful difference. It also does not report individual participant data, so the spread and pattern of paired changes cannot be reconstructed from the arm means alone.

What do standard deviations describe?

A standard deviation describes how spread out observations are around their mean. A larger standard deviation indicates more variability in the observed scores. It is not the same as a standard error: the standard deviation concerns variation among observations, while a standard error describes uncertainty in an estimated quantity such as a mean. The reported primary standard deviations are 1.11 for lisdexamfetamine and 1.47 for placebo. Neither value alone indicates how precise the difference between means is.

In general, the standard error of a mean depends on both the variability of observations and the number of observations. For a crossover trial, the uncertainty of a within-person contrast can also depend on the correlation between a participant’s scores in the different periods. The registry record does not report that correlation or a paired estimate. The posted unadjusted comparison is based on summary statistics, and its relation to a crossover-aware analysis cannot be confirmed from the record.

How should the confidence interval be read?

A confidence interval gives a range of estimates compatible with the observed data under the method’s assumptions. In repeated use, a 95% confidence interval procedure would capture the true parameter in 95% of comparable repetitions if its assumptions were met. That general interpretation does not mean there is a 95% probability that this particular interval contains the true effect. The primary interval includes zero, so the posted data do not distinguish the estimate clearly from no difference under this calculation.

The interval’s width conveys precision: a narrower interval indicates more precision, while a wider interval indicates less. Precision is not the same as clinical importance. An estimate can be precise but small, or imprecise while including effects in both directions. The primary estimate should therefore be read together with its interval, the endpoint definition, and the analysis limitations.

What does the p-value add?

The unadjusted p-value for the primary comparison was 0.093. In general, a p-value is calculated under a null hypothesis and a statistical model. It describes how often results at least as incompatible with that null model might occur under the assumptions. It does not measure the size or importance of a difference, and it does not give the probability that the result arose by chance. The registry record does not report a multiplicity-adjusted p-value or the model used for a formal sponsor analysis.

The term unadjusted matters because it indicates that the reported p-value does not account for testing multiple outcomes or comparisons. With 23 outcome measures listed, the chance of at least one apparently notable result can increase when many tests are considered. General statistical practice addresses this through prespecified hierarchies, adjusted procedures, or cautious interpretation. Which approach was intended for this trial is not reported in the registry record.

Why does the crossover structure matter?

In a crossover study, participants receive multiple conditions in sequence. Their own outcomes under different conditions can serve as a within-person comparison, reducing the influence of stable differences between participants when the analysis is designed to use pairing appropriately. However, valid interpretation may depend on treatment order, period effects, carryover, and the time between conditions. These are general design considerations, not details confirmed for this study.

The registry record identifies the trial as crossover but does not report sequence allocation, washout, period-specific outcome data, or an analysis model. The arm summaries report means, standard deviations, and observation counts, but do not provide the covariance needed to recover a paired treatment contrast. Therefore, an unadjusted calculation from the posted summaries cannot be assumed to capture all features of the crossover design.

The record lists 16 observations for lisdexamfetamine and 17 for placebo on the primary measure. Those figures do not, by themselves, say how many participants contributed paired observations, whether every participant completed both periods, or how incomplete records were handled. The population note records one placebo-arm completer who dropped out of the lisdexamfetamine arm due to an adverse event, but a complete account of analysis inclusion is not reported.

What is and is not reported?

The registry contains posted arm means and standard deviations for the primary endpoint and several secondary outcomes, along with unadjusted comparisons. It lists zero reported analyses. A detailed statistical analysis plan, model specification, baseline adjustment, missing-data procedure, treatment-sequence analysis, and multiplicity strategy are not reported in the registry record. The original sample-size rationale is also not reported.

General statistical interpretation distinguishes an analysis specified before examining results from a calculation made from summary results. Prespecification helps limit selective emphasis and clarifies which outcome and method are intended to answer the main question. Without the original plan, it is not possible to determine whether the posted calculations reproduce the investigators’ intended primary analysis.

The registry record does not report a discrepancy between the posted summaries and recalculated comparisons. That absence does not resolve the separate limitations arising from unreported analysis details. The comparison should be understood as an unadjusted summary-based estimate rather than as a fully documented analysis of the crossover trial.

11. Confidence Intervals and Precision

The primary mean difference was -0.76, with a confidence interval from -1.646 to an upper limit just above zero. The interval includes zero, so the result is compatible with no difference under the calculation used. It is also compatible with a range of negative differences, and a small positive difference. The interval therefore indicates uncertainty about both the size and direction of the comparative effect.

Precision is influenced by the variability of scores and the amount of information available. The primary arm standard deviations were 1.11 and 1.47, and the posted arm observation counts were 16 and 17. These summaries help describe the data, but they do not communicate the within-participant covariance that can be relevant to a crossover analysis. The confidence interval is based on the posted unadjusted comparison, not on a reported crossover-specific model.

An interval that includes zero is not evidence that the treatments are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the plausible effect lies within that margin. Such a margin and analysis are not reported in the registry record. Likewise, the interval should not be treated as a probability distribution for the true effect.

The estimate is expressed in standardized-score units, which makes it possible to describe the size relative to the scale’s standardization, but the record does not define a threshold for a meaningful change. Statistical uncertainty and practical importance are separate questions. The posted interval supports a cautious conclusion: the observed data do not estimate the comparative difference precisely enough to exclude no difference, and the registry record lacks analysis details that could clarify the crossover comparison.

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 participants per arm for 80% power and participants per arm for 90% power. They are planning illustrations based on the observed effect, not the trial’s original design assumptions. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect.

For the primary endpoint, planning for 100% of the observed effect gives 47 participants per arm for 80% power and 63 participants per arm for 90% power. Planning for 75% of the observed effect gives 83 participants per arm for 80% power and 111 participants per arm for 90% power. Planning for 50% of the observed effect gives 187 participants per arm for 80% power and 250 participants per arm for 90% power.

In plain terms, 80% power means that, under the planning assumptions and if the specified effect were the true effect, the design would have an 80% chance of detecting a difference using the stated test threshold. The 90% column describes the corresponding planning target with a higher chance of detection. Smaller effects are harder to distinguish from random variation, so they require more participants under these assumptions. The curve expresses this general relationship between the effect targeted and the participant requirement.

These figures are not observed power. They do not show the probability that the trial’s result is correct or that the treatment has an effect. The registry record does not report the sample-size assumptions used when the trial was designed, so these planning illustrations should not be read as a reconstruction of the investigators’ original rationale.

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 = -0.760; pooled standard deviation σ = 1.308.
2. n = 2 × (1.96 + 0.842)² × 1.308² / -0.760² = 46.5, rounded up to 47 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 <- -0.76                      # observed difference in means
sigma <- 1.30823569939109                     # 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(2712996)
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 = 47 (80% power), 63 (90% power)
 75% of observed effect: n per arm = 83 (80% power), 111 (90% power)
 50% of observed effect: n per arm = 187 (80% power), 250 (90% power)
power.t.test: 47.5 
Simulated power at n = 47 per arm: 0.797 (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 lists 23 outcome measures and reports zero analyses. It identifies the Conners-3 Parent Form inattention scale as the primary outcome and lists multiple secondary measures. It does not report a multiplicity plan, such as an adjustment for testing many outcomes, a prespecified hierarchy, or a rule for interpreting secondary findings. Without that information, the risk of chance findings across multiple comparisons cannot be assessed from the record.

Multiplicity matters because each statistical test can produce an apparently unusual result by chance. When many tests are performed, the chance of at least one such result can rise. Adjustment procedures or a clear hierarchy can help control that risk, but they involve choices that need to be specified and interpreted in context. No such procedure is reported for this trial, so unadjusted secondary results should be treated cautiously and should not be promoted as confirmatory evidence.

The record does not report a full analysis population definition. It provides arm-specific outcome counts and notes that one participant completed placebo but dropped out of the lisdexamfetamine arm due to an adverse event. It does not give a complete participant flow, reasons for any other missing observations, or an account of whether participants were analyzed according to randomized sequence, treatment received, or outcome availability.

Missing data can affect estimated means when the likelihood of missingness is related to outcomes, treatment, or participant characteristics. In general, methods for handling missing data rely on assumptions, and results may differ depending on those assumptions. The registry record does not report the method used, sensitivity analyses, or whether the primary analysis included all randomized participants.

The crossover design adds further relevance to missingness: incomplete participation in one period can limit the availability of within-person comparisons. The record does not report how incomplete crossover records were handled or whether participants with only one period contributed to the primary comparison. Treatment sequence, period effects, baseline adjustment, and the formal analysis model are also not reported. These omissions limit assessment of the statistical robustness of the posted results.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures list 17 participants at risk in each arm. No serious adverse events affecting participants are reported in either arm, and deaths are listed as zero in both arms. The record also lists no serious adverse event terms. These counts describe what was entered in the registry safety results; they do not establish that no other safety outcomes occurred.

For other, non-serious adverse events, 1 participant is listed as affected in the lisdexamfetamine arm and 0 in the placebo arm, with 17 at risk in each arm. The primary outcome population note separately states that one participant completed placebo but dropped out of lisdexamfetamine due to an adverse event. The record does not provide enough detail to identify the event or establish whether the listed non-serious adverse event is the same event referenced in that note.

These safety counts are descriptive and are based on the reporting in the registry. They do not compare risks with precision, especially in a small trial, and they do not establish that either treatment is safe or unsafe. Details such as event type, timing, severity beyond the serious classification, and relatedness for the non-serious event are not reported in the registry record.

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

The registry results describe a randomized, triple-masked crossover comparison of lisdexamfetamine and placebo in children with traumatic brain injury-related attention deficits. For the primary parent-rated inattention outcome, the posted mean was lower in the lisdexamfetamine arm than in the placebo arm, and the unadjusted mean difference was -0.76. The interval includes zero, so the comparison does not provide a precise distinction from no difference under the calculation used.

This result does not establish that lisdexamfetamine improves attention, and it does not establish that it has no effect. An uncertain estimate is different from evidence of equivalence. The registry record does not report an equivalence margin, a sponsor analysis, or a detailed crossover-aware model that would support stronger conclusions. The posted summary calculation should therefore be interpreted with the design and reporting limitations in mind.

The trial was designed for children with attention deficits associated with traumatic brain injury, not necessarily for all children with attention difficulties or for all people with traumatic brain injury. The summary describes the intended ages as 6-16, while the outcome instrument description refers to children aged 6 to 18 years. The record does not give enough detail to characterize the enrolled participants or determine how broadly the findings apply.

The study’s posted outcome data are one part of the evidence, not a complete answer about treatment. The number of reported outcomes, unreported multiplicity approach, incomplete participant-flow information, and absent details on missing-data handling all limit interpretation. The crossover design can provide useful within-person comparisons when analyzed appropriately, but the registry record does not report enough about sequencing or analysis to verify how that design was used.

The safety entries report no serious adverse events and one non-serious adverse event affecting a participant in the lisdexamfetamine arm, with none listed for placebo. These descriptive counts do not establish comparative safety. Taken together, the record supports a cautious reading of the observed scores and uncertainty, rather than a definitive clinical conclusion.

17. Why This Trial Matters Statistically

This trial illustrates why a numerical difference and a statistical conclusion are not the same thing. The primary estimate is negative, meaning the posted standardized mean was lower in the lisdexamfetamine arm under the stated contrast. Yet the confidence interval includes zero, so the estimate remains uncertain. Reading only the direction or the point estimate would omit important information about precision.

The crossover design also highlights the need for analysis methods that match the way a trial is organized. Repeated measurements from the same participant can be informative, but they are correlated. An analysis that accounts for the pairing may differ from a calculation based on separate arm summaries. The registry record identifies the crossover model, but does not report the details needed to evaluate how participant-level pairing, period, or sequence were handled.

Multiplicity is another statistical issue made visible by the record. With 23 outcomes listed, a clear distinction between a primary question and exploratory secondary assessments matters. The primary endpoint is identified, but no multiplicity procedure or hierarchy is reported. This limits how strongly secondary findings can be interpreted and underscores the value of transparent analysis plans.

Finally, sample-size planning should not be confused with the result of the trial. The planning figures illustrate how participant requirements change when the effect targeted is smaller, under stated assumptions. They are not the trial’s original justification and do not describe observed power. The original design assumptions are not reported in the registry record. Together, these points show how design, estimation, precision, multiplicity, and reporting shape the conclusions that can be drawn from clinical trial data.

18. Limitations

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

Several limitations specific to this record constrain interpretation. Although the trial is identified as crossover, the registry does not report the treatment sequence, period order, washout arrangements, or treatment-period results. It is therefore not possible to assess carryover or period effects, or to determine whether the posted comparison uses the within-participant structure appropriately.

The record reports an unadjusted comparison based on summary statistics and lists zero reported analyses. It does not describe the statistical model, baseline adjustment, analysis population, or handling of missing data. The primary population note records a dropout from the lisdexamfetamine arm due to an adverse event after completing placebo, but there is no complete account of participant flow or the consequences for analysis inclusion.

The record also lacks a reported multiplicity strategy despite listing 23 outcomes. This makes secondary comparisons particularly difficult to interpret as confirmatory evidence. The original sample-size justification and assumptions are not reported; the available planning figures are illustrations based on the observed effect and specified planning assumptions, not the trial’s design rationale.

The enrollment is listed as 20, while primary outcome arm counts are 16 and 17. These figures are not a substitute for a participant-flow description, and the registry record does not reconcile them or explain who contributed to each result. The intervention period is described as 6 weeks for each condition, while the primary outcome timeframe is 12 weeks; the record does not explain the schedule connecting those descriptions.

Finally, the outcome is a parent-rated symptom measure reported as a z-score. The record does not identify the standardization reference or define a clinically meaningful difference. These limits do not invalidate the posted summaries, but they restrict the conclusions that can be drawn from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Treatment of Traumatic Brain Injury (TBI)-Related Attention Deficits in Children — NCT02712996.
• Registry record last updated 2020-07-13; status last verified 2020-06.
• Results first posted 2020-07-13.
• 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 Phase 4 randomized, triple-masked crossover trial sponsored by Vanderbilt University. It lists an enrollment of 20 and evaluates morning lisdexamfetamine, 20-70 mg for 6 weeks, against a placebo capsule. The intended population is children with traumatic brain injury-related attention deficits.

The primary outcome was the Conners-3 Parent Form inattention score at 12 weeks, reported as a z-score. Posted means were 1.0 for lisdexamfetamine and 1.76 for placebo; the unadjusted mean difference was -0.76, with an interval that includes zero and an unadjusted p-value of 0.093. The record lists 23 outcome measures and zero reported analyses.

The registry reports no serious adverse events or deaths in either arm and lists one non-serious adverse event affecting a participant in the lisdexamfetamine arm. Crossover analysis details, multiplicity procedures, missing-data methods, and the original sample-size rationale are not reported in the registry record.