TRI102 in the Treatment of Children With Attention Deficit Hyperactivity Disorder (ADHD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for TRI102 in the Treatment of Children With Attention Deficit Hyperactivity Disorder (ADHD) (NCT02083783), a randomized phase 3 study. The primary outcome is SKAMP (Swanson, Kotkin, Agler, M-Flynn, and Pelham Scale).

2. Clinical Question

3. Trial Design

The registry describes a Phase 3 randomized, quadruple-masked, parallel-group study comparing TRI102 with placebo. Its title identifies a laboratory classroom study, and its stated purpose was to determine whether TRI102 was effective in children ages 6–12 with ADHD. The study status is completed. The listed start was 2014-03 and the primary completion was 2014-10.

The registered enrollment was 108. The primary outcome results are presented for an intention-to-treat population, with arm summaries reporting 51 for TRI102 and 48 for placebo. The record does not explain the difference between the enrollment figure and the arm counts in the posted outcome summary, so the reason for that difference is not reported in the registry record. Nor does the information available for this analysis specify the detailed handling of missing outcome observations.

TRI102 is described as an active amphetamine extended-release oral suspension; the comparator is placebo. The study record labels the allocation randomized and the design parallel. “Quadruple” is the recorded masking category, but the specific people or roles covered by masking are not reported in the registry record. Further details on the randomization procedure, allocation concealment, treatment administration, or classroom procedures are also not reported in the registry record.

The primary measure was change from baseline in the SKAMP-Combined score, assessed approximately 4 hours after dose. The record also lists PERMP, a measure of questions answered correctly, as a secondary outcome. The registry lists two outcome measures and two analyses overall, and one secondary outcome is posted in the record. The study’s original sample-size rationale, its prespecified statistical analysis plan, and any planned interim analyses 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: 8 subjects not randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention to treat population

5. Baseline Characteristics

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

Population: Intent-to-treat population

6. Primary Endpoint

The registry lists the primary outcome as SKAMP (Swanson, Kotkin, Agler, M-Flynn, and Pelham Scale), measured over Absolute change from baseline in SKAMP-C score from baseline to 4 hours after dose.

The primary endpoint was absolute change from baseline in SKAMP-Combined score from baseline to approximately 4 hours after dose. SKAMP combines 13 assessment items. Each item is rated on a 7-point scale, from 0 for normal to 6 for maximal impairment, and the combined score ranges from 0 for normal to 78 for maximal impairment. The endpoint therefore summarizes classroom-related symptoms and behavior on a continuous scale, with higher scores indicating greater impairment.

A change score expresses how far the recorded score moved from the participant’s baseline value. In general, a negative change on this scale indicates a lower score at the later assessment than at baseline, while a positive change indicates a higher score. The reported mean change was -9.1 for TRI102 and 5.6 for placebo. These group summaries describe average change, not the pattern for every participant.

Using a standardized scale provides a common way to summarize the outcome across participants and compare groups. A measurement at a specified time after dose makes the comparison time-specific: it addresses the registered assessment at approximately 4 hours, rather than change over an unspecified period. The endpoint is relevant to the study’s classroom setting, but the registry record does not establish how well this single assessment represents experiences in other settings or at other times. The posted endpoint is a score change, not a direct measure of longer-term outcomes.

7. Results Posted in the Registry

• TRI102: mean -9.10 versus 5.60 on control; difference -14.70 (95% CI -17.73 to -11.67), standardized effect d = -1.91; z-test p = <0.001.

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.

PERMP (Permanent Product Measure of Performance).

• 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 errors.
• Result:
  • TRI102: mean 25.30 versus -13.60 on control; difference 38.90 (95% CI 26.98 to 50.82), standardized effect d = 1.29; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for TRI102 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts one secondary outcome, PERMP, which measures questions answered correctly. Its recalculated comparison is positive for TRI102 relative to placebo, consistent in direction with the primary comparison when each outcome is interpreted on its own scale. The sponsor’s reported PERMP estimate is also positive. This offers a related measure of performance alongside the primary SKAMP result, but the outcomes measure different aspects of the study and use different scales.

The secondary outcome can add context to the primary finding because it concerns performance in the same general study setting and assessment period. Agreement in direction across these measures does not make them interchangeable, nor does it prove that either measure captures every clinically relevant outcome. The primary endpoint remains the registered main outcome; a secondary endpoint should not be used to redefine the main question after results are known.

Unadjusted secondary results carry less weight because evaluating more than one outcome can increase the chance of finding a nominally significant result by chance. In general, multiplicity procedures or a prespecified hierarchy can address that concern, but the registry record does not report whether either was used. The existence of a secondary result does not establish that it was confirmatory. The registry lists two outcome measures and two analyses overall, while one secondary outcome is posted; the details of any additional measure or analysis are not reported in the registry record.

For that reason, the secondary pattern is best treated as supporting context rather than as a separate, definitive test of the primary conclusion. Its interpretation depends on the analysis plan, measurement properties, missing-data handling, and the relationship between the outcomes. Those details are not fully reported in the registry record. The direction of the posted secondary comparison can be described, but its evidential strength should not be overstated.

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

• PERMP (Permanent Product Measure of Performance).

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a score that can take a range of values rather than an event counted as yes or no. The posted arm summaries give a mean change and a standard deviation for each group. The mean describes the group’s average change. The standard deviation describes how dispersed participants’ change scores were around that average. In general, these answer different questions: a mean summarizes the group location, while a standard deviation summarizes variation among observations.

What does the mean difference represent?

The reported unadjusted mean difference compares the average change in the TRI102 group with the average change in the placebo group. The estimate is -14.7. Its sign depends on the subtraction order, which is TRI102 minus placebo. Since lower SKAMP scores indicate less impairment, a negative contrast means the average change was lower in the TRI102 group than in the placebo group. This is a comparison of group means, not a claim that all participants changed by that amount.

The recalculated comparison is unadjusted: it uses the posted arm-level means, standard deviations, and group sizes without controlling for baseline or other covariates. This is useful as a transparent check of the summary statistics, but it is not the same model as an adjusted analysis. An ANCOVA, the method named for the registry’s reported analysis, generally compares outcomes while adjusting for specified covariates. In general, adjustment can change the estimate or its precision, depending on the model and the data. The covariates and full model specification are not reported in the registry record, so the ANCOVA cannot be reconstructed from the information available.

What does a p-value tell the reader?

The primary recalculated unadjusted p-value is <0.001, and the sponsor-reported p-value is < 0.001. In general, a p-value measures how incompatible the observed data, or more extreme data, would be with a specified null model. It is not the probability that the null hypothesis is true, and it does not measure the probability that the observed effect will recur. A small p-value is evidence against the null model under the assumptions of the analysis. It does not by itself communicate the magnitude, precision, clinical relevance, or generalizability of a result.

The registry labels the sponsor analysis as a superiority analysis. That label describes the analysis objective, not a guarantee about the interpretation or importance of the result. In general, superiority testing evaluates whether one group’s outcome differs in a specified favorable direction from the comparator, using a prespecified statistical framework. The full framework, including covariate choices and any multiplicity approach, is not reported in the registry record.

Why do confidence intervals matter?

A confidence interval gives a range of estimates compatible with the data under the method’s assumptions and conveys uncertainty around an estimate. In general, a narrower interval indicates greater statistical precision than a wider interval for the same quantity and method. The recalculated primary interval is -17.73 to -11.67. The sponsor-reported 95% interval is -17.9 to 11.6; as recorded, its upper bound is on the opposite side of zero from its estimate. The record does not resolve that mismatch. The two intervals are results from different calculations and should not be conflated.

Intervals depend on the analysis method and its assumptions. The recalculated interval is unadjusted, whereas the registry names ANCOVA for the sponsor analysis. Differences between methods may affect interval width and endpoints. In this case, the unusual sponsor-reported upper bound raises an interpretation issue that cannot be settled from the registry record alone. The reported point estimate and p-value remain as posted, but the interval should be quoted accurately and its inconsistency made clear.

What is the role of the secondary outcome?

PERMP measures questions answered correctly, with the posted outcome framed as change from baseline. Its recalculated mean difference is 38.9 and its unadjusted p-value is <0.001. The arm-level spreads are standard errors rather than standard deviations. A standard error describes uncertainty in an estimated mean, whereas a standard deviation describes variation among individual observations. The record does not report a standard deviation for this secondary measure. The recalculated standard deviation used for the standardized comparison is marked approximate because it is inferred from standard errors; it is not a directly posted group standard deviation.

In general, testing multiple outcomes or multiple contrasts creates more opportunities for apparently small p-values. If no adjustment or prespecified hierarchy controls that issue, unadjusted secondary results are less conclusive than a single prespecified primary result. Whether the sponsor used such procedures is not reported in the registry record. The secondary result can be considered alongside the primary outcome for context, but it should not be treated as an independent confirmation without knowing the analysis plan and multiplicity handling.

All statistical interpretation also relies on design and data-handling choices. Randomization supports a group comparison in principle, while masking can reduce some forms of bias; the record’s labels alone do not document how those safeguards were implemented. The analysis population is named as intention to treat for the primary outcome, but detailed rules for missing observations, exclusions, or model diagnostics are not reported in the registry record. Statistical methods should therefore be read together with the available design description and the limits of the registered detail.

11. Confidence Intervals and Precision

The recalculated unadjusted primary mean difference is -14.7, with an interval from -17.73 to -11.67. This interval lies entirely below zero and is relatively concentrated around the estimate under the unadjusted calculation. It conveys uncertainty about the group mean contrast, not the range of individual participant changes. Its interpretation depends on the calculation’s assumptions and should not be confused with the sponsor’s adjusted ANCOVA result.

The registry reports a 95% confidence interval of -17.9 to 11.6 for the ANCOVA estimate of -14.68. Because the upper endpoint is positive, the interval as recorded crosses zero, unlike the recalculated interval. It also does not align with the reported p-value of < 0.001 in the usual way. The registry record does not clarify whether this is a transcription, formatting, or analytic issue. The endpoint should therefore be quoted exactly as recorded and treated cautiously rather than replaced with a presumed correction.

In general, a confidence interval expresses the range of values that remain compatible with the data under the method used; it is not a guarantee that the true value lies inside that particular interval. Precision is affected by sample size, variability, and model choices. The posted primary arm standard deviations are 7.51 and 7.85, and the recalculated comparison uses 51 and 48 in the respective arms. Those figures help describe the calculation, but do not resolve the inconsistency in the sponsor-reported interval.

The secondary PERMP recalculated interval is 26.98 to 50.82 around the estimated difference of 38.9. The sponsor-reported 95% interval for that analysis is 27.3 to 50.6, with p < 0.001. Both intervals are positive and close in their endpoints, unlike the primary sponsor interval. This consistency does not change the different evidential status of a secondary endpoint or address any unreported multiplicity procedure.

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, not total events. They are illustrations calculated from the observed effect under the stated assumptions: a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrated participants per arm for a design with an 80% chance of detecting the chosen effect under those assumptions, if that effect and the model assumptions hold. The 90% power column uses a higher target chance of detection and consequently gives larger planning figures for the listed scenarios. These are design calculations, not descriptions of the observed trial’s ability to detect an effect. This is not observed power.

For the primary outcome, the planning figures range from 5 participants per arm for 80% power and 6 for 90% power when planning for 100% of the observed effect, to 18 and 23 when planning for 50% of the observed effect. Planning for 75% of the observed effect gives 8 for 80% power and 11 for 90% power. The secondary-outcome illustrations are also based on fractions of its observed effect and are reported separately.

The general pattern is important: smaller effects need more participants to detect, all else equal. These figures are sensitive to the observed effect used as their starting point. They should not be read as evidence that the original study was designed around those assumptions, nor as proof that an effect of a particular size would be detected reliably in another study. The registry record does not report the original planning 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 = -14.700; pooled standard deviation σ = 7.677.
2. n = 2 × (1.96 + 0.842)² × 7.677² / -14.700² = 4.3, rounded up to 5 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 <- -14.7                      # observed difference in means
sigma <- 7.67662303601742                     # 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(2083783)
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 = 5 (80% power), 6 (90% power)
 75% of observed effect: n per arm = 8 (80% power), 11 (90% power)
 50% of observed effect: n per arm = 18 (80% power), 23 (90% power)
power.t.test: 5.4 
Simulated power at n = 5 per arm: 0.753 (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 registry’s sponsor analysis for the primary outcome is an ANCOVA comparing final values. It reports a mean difference of -14.68, a p-value of < 0.001, and a 95% confidence interval of -17.9 to 11.6. The unadjusted recalculation from the posted summary statistics gives a mean difference of -14.7, a p-value of <0.001, and an interval from -17.73 to -11.67.

The point estimates are close, but the methods differ: the recalculation is unadjusted, while the sponsor names ANCOVA. The registry does not report the covariates or model details needed to reproduce the sponsor analysis. The interval endpoints are not close, and the sponsor interval’s positive upper bound is inconsistent with the negative point estimate and small p-value in the usual interpretation. This discrepancy is present in the values as recorded; the registry record does not explain it. The sponsor interval should not be silently altered or replaced by the recalculated interval.

For PERMP, the sponsor reports an ANCOVA estimate of 38.9, a 95% interval of 27.3 to 50.6, and p < 0.001. The unadjusted recalculation gives 38.9, an interval of 26.98 to 50.82, and p < 0.001. These values are similar, but they remain outputs from distinct analyses. The posted sponsor results are the registry’s reported analyses; recalculated values are simple checks based on the summary statistics and do not substitute for the sponsor’s model.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary outcome and a secondary outcome, but does not report a complete statistical analysis plan or explain how testing across outcomes was handled. In general, when several hypotheses are tested, the chance of at least one small p-value can increase if each is judged separately at the same threshold. Multiplicity adjustments, hierarchical testing, or a clearly prespecified distinction between confirmatory and exploratory outcomes can address this issue. Whether such a procedure was used is not reported in the registry record.

The primary result has a clearer status because SKAMP is identified as the primary outcome. The PERMP result is secondary, so its unadjusted p-value should be interpreted more cautiously unless the study’s prespecified plan establishes how it fits into the testing strategy. The record does not provide enough information to determine whether the posted secondary result was intended as confirmatory, how any additional outcome was handled, or whether there were other analyses that could affect interpretation.

The primary analysis population is described as intention to treat. That label indicates the stated population for the analysis, but the registry record does not describe the exact analysis population rules, the number of participants with observed endpoint data, or how missing outcomes were handled. It also does not report whether imputation, sensitivity analyses, or other missing-data procedures were used. The enrolled count and posted arm counts do not, by themselves, explain missingness or exclusions.

In general, missing-data methods matter because the analysis can be influenced if outcome availability is related to treatment assignment, outcome values, or participant characteristics. The registry record does not give enough detail to assess those possibilities. Further, the adjustment variables and diagnostics for the sponsor’s ANCOVA are not reported. These gaps limit independent evaluation of the analysis, even though randomization and the named analysis population provide useful design context.

Interim analyses, stopping rules, and the original statistical plan are not reported in the registry record. Their absence from the record should not be taken as evidence that they did or did not occur. Without those details, the results can be interpreted as the posted analyses, while the full safeguards against multiplicity, missing-data bias, and analysis flexibility remain uncertain.

16. 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 3% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists serious adverse events for 0 participants in the TRI102 group and 0 in the placebo group. The number assessed for serious adverse events is reported as 52 for TRI102 and 48 for placebo. The record lists no deaths in either group. These are the posted serious-event counts and should be read with their reported group denominators.

For other adverse events, the registry lists 6 affected participants among 52 at risk for TRI102 and 1 among 48 at risk for placebo. These are counts, not a complete description of event type, duration, severity, or relationship to study treatment. The record does not provide a list of serious-event terms because no serious adverse events are listed, and it does not provide enough detail to assess all safety outcomes.

In general, a zero count in a study does not establish that an event cannot occur; the observed counts describe what was recorded in this study. Group differences in counts should not be interpreted in isolation from study size, follow-up, event definitions, and completeness of reporting. The registry record does not provide further detail on these matters in the information available for this analysis. These safety counts are descriptive and do not support medical advice.

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

The posted primary results describe a difference in average SKAMP-C change between the randomized groups at approximately 4 hours after dose. The TRI102 group’s mean change was -9.1, compared with 5.6 for placebo, and the unadjusted mean difference was -14.7. On a scale where higher scores represent more impairment, that contrast points toward a lower average score in the TRI102 group at the assessment. It is a group-level statistical result, not a prediction of an individual participant’s outcome.

The result does not establish what happens at other assessment times, in settings outside the laboratory classroom study, or over a longer period. The registry’s stated population is children ages 6–12 with ADHD, and the findings should not automatically be extended beyond that population. The record also does not provide enough detail to assess the representativeness of the enrolled participants or the transportability of the result to other circumstances.

The primary result does not by itself establish how meaningful the score difference is to children, families, or clinicians. The registry record does not provide a threshold for interpreting a meaningful change, nor does it report long-term outcomes in the information available for this analysis. Statistical evidence and practical importance are related but distinct questions. A small p-value does not quantify benefit, reveal how many individuals changed, or resolve uncertainties about measurement and generalizability.

The interpretation also has a precision caveat. The recalculated unadjusted interval is entirely negative, while the sponsor-reported interval has a positive upper endpoint despite a negative estimate and p < 0.001. The registry record does not explain this inconsistency. That issue limits a straightforward reading of the sponsor’s reported precision and should remain visible when describing the result.

Finally, the record does not report the original sample-size rationale, detailed missing-data procedures, the full adjusted model, or multiplicity handling. Those omissions do not erase the posted findings, but they constrain how completely the analysis can be independently assessed. The appropriate interpretation is a specific comparison of posted outcomes in this trial, with uncertainty about aspects of design implementation and analysis detail left unresolved by the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why the direction and scale of an endpoint matter. SKAMP-C runs from normal to maximal impairment, so negative change represents movement toward a lower score, while a positive change represents movement toward a higher score. Reading the group contrast without understanding that scale could reverse its meaning. The posted arm means and their contrast need to be interpreted together with the endpoint definition.

It also shows why the point estimate, p-value, and confidence interval should be considered jointly. The unadjusted recalculation and sponsor analysis have close primary point estimates, but their reported intervals differ sharply, and the sponsor interval as recorded does not align with the direction of its estimate and p-value. A strong-sounding significance result does not remove the need to check whether the precision statistics are internally coherent.

The distinction between unadjusted and adjusted analyses is another useful statistical lesson. Summary statistics allow a transparent recalculation, while ANCOVA may account for covariates. Without the sponsor model details, the adjusted result cannot be independently reconstructed. Reporting both types of analysis can inform interpretation, but their estimates and intervals should not be treated as if they came from the same calculation.

Finally, the secondary endpoint and planning illustrations show the importance of separating evidence from context. A directionally consistent secondary result may add context, but unreported multiplicity methods limit how strongly it can be treated as confirmation. Planning figures derived from observed effects illustrate how assumed effect size changes sample-size requirements, but they do not reveal the trial’s original design rationale or observed power. Together, these points make the record a useful example of both what summary results can convey and what they cannot settle.

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 several trial-specific details unresolved. It does not report the detailed randomization procedure, allocation concealment, which roles were included in quadruple masking, or how masking was implemented. The laboratory classroom setting and the specified assessment time define the context of the primary result, but the record does not establish how closely that context represents other settings or longer-term experience.

The primary outcome arm summaries report 51 for TRI102 and 48 for placebo, whereas registered enrollment is 108. The record does not explain the relationship between these counts. This difference should not be assigned a cause without further information; it does not, on its own, establish dropout, missingness, or exclusion. The rules defining the intention-to-treat analysis population and the handling of missing observations are not reported in the registry record.

The sponsor’s ANCOVA point estimate is close to the unadjusted recalculation, but the reported 95% confidence interval has an upper bound of 11.6, which is positive despite the negative estimate and p < 0.001. The registry record does not clarify this apparent inconsistency. The recalculated interval cannot be used to silently repair the sponsor result, and the adjusted model cannot be reproduced because its covariates and full specification are not reported.

The registry does not report the original sample-size justification, the prespecified multiplicity strategy, interim analyses, missing-data sensitivity analyses, or detailed outcome-assessment procedures. Only one secondary outcome is posted, although the record lists two outcome measures overall. The record does not explain the unposted measure or its analysis. These gaps limit assessment of outcome selection, analysis flexibility, and the strength of secondary findings. They are limitations of what the registry record documents, not proof that a particular procedure was absent.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: TRI102 in the Treatment of Children With Attention Deficit Hyperactivity Disorder (ADHD) — NCT02083783.
• Registry record last updated 2020-08-26; status last verified 2020-08.
• Results first posted 2020-08-26.
• 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

This completed Phase 3 study was a randomized, quadruple-masked, parallel-group comparison of TRI102 and placebo in children with ADHD. The primary endpoint was change from baseline in SKAMP-Combined score approximately 4 hours after dose, analyzed in the intention-to-treat population. The posted mean changes were -9.1 for TRI102 and 5.6 for placebo.

The recalculated unadjusted mean difference was -14.7, with an interval from -17.73 to -11.67 and p < 0.001. The sponsor-reported ANCOVA estimate was -14.68 with p < 0.001, but its recorded 95% interval of -17.9 to 11.6 has a positive upper endpoint and is not explained by the registry record. PERMP was posted as a secondary outcome with a positive estimated comparison for TRI102.

The registry reports no serious adverse events and no deaths in either group. Interpretation is limited by unreported details about the analysis plan, missing data, multiplicity, and the sponsor model, as well as the unresolved primary confidence-interval inconsistency.