Study to Evaluate Safety & Efficacy of d-Amphetamine Transdermal System vs Placebo in Children & Adolescents With ADHD: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate Safety & Efficacy of d-Amphetamine Transdermal System vs Placebo in Children & Adolescents With ADHD (NCT01711021), a randomized phase 2 study. The primary outcome is Mean Swanson, Kotkin, Agler, M-Flynn, and Pelham (SKAMP) Total Score During the Double-Blind Treatment Period.

2. Clinical Question

3. Trial Design

The registry describes a Phase 2, randomized, triple-masked study with a sequential model. Its official title identifies it as a double-blind, placebo-controlled crossover laboratory classroom study. The recorded enrollment is 110, and the study status is completed. The study start is listed as 2012-10 and primary completion as 2013-03.

The available arm descriptions outline two parts: a 5-week, open-label, step-wise dose optimization period, followed by a 2-week randomized crossover double-blind treatment period. Participants who reached an optimal dose by the end of dose optimization were randomized to double-blind treatment. The arm descriptions are incomplete in the registry record, so further details of treatment order, washout, dosing, or the precise crossover schedule are not reported in the registry record.

The primary outcome was mean SKAMP total score during the double-blind treatment period. The stated timeframe describes a mean based on SKAMP total scores at 9 post-dose time points, from 1 through 12 hours. The primary analysis population is defined as the Full Analysis Set: consented and randomized subjects who took at least one dose of study medication. Outcome-specific analysis counts vary, and the registry does not explain all differences between those counts.

Several secondary outcomes are also listed, including SKAMP onset and duration measures, performance scores, ADHD symptom ratings, parent ratings, and clinical global impression responders. The registry record does not report the original sample-size justification, detailed randomization sequence, allocation ratio, or the complete statistical analysis plan.

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: The study consisted of 2 study periods. Period 1 is a 5-week open-label Dose Optimization Study with only one arm, Period 2 is a randomized, cross-over, double-blind treatment study (2 weeks). A total of 110 subjects were enrolled into the Dose Optimization Treatment (Period 1). 4 subjects did not complete the Dose Optimization Period. 106 subjects were randomized into the Double-Blind Treatment Period (Period 2).

Open-Label Dose Optimization Period

Double-blind Cross-Over Treatment Period

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set: included all consented and randomized subjects who took at least 1 dose of study of medication

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: A total of 110 subjects entered the Dose Optimization Period. The optimized dose achieved by a subject during this period was then utilized in the Double-Blind Treatment Period of the study. The Demographic and Baseline Characteristics are presented as one arm for all subjects enrolled.

6. Primary Endpoint

The registry lists the primary outcome as Mean Swanson, Kotkin, Agler, M-Flynn, and Pelham (SKAMP) Total Score During the Double-Blind Treatment Period, measured over Mean SKAMP Total Score of SKAMP Total Scores from 9 different time points including (1, 2, 3, 4.5, 6, 7, 9, 10, 12 hours post-dose).

The primary endpoint was mean Swanson, Kotkin, Agler, M-Flynn, and Pelham (SKAMP) total score during the double-blind treatment period. The SKAMP is designed for independent observers to rate classroom behavior. Its 13 items cover attention and deportment, as well as quality of work. Attention items concern starting and sustaining tasks, attending to activities, and moving between activities. Deportment items concern interactions, remaining quiet, and staying seated according to classroom rules. The quality-of-work items concern completing work, accuracy, and care in writing or drawing.

The record describes a mean of SKAMP total scores collected at 9 post-dose time points, including 1, 2, 3, 4.5, 6, 7, 9, 10, and 12 hours. The scale ranges from 0-78, with higher scores indicating worse impairment. Thus, a lower score represents a lower rated level of classroom-behavior impairment on this measure; it is not itself a direct measure of every aspect of ADHD or daily functioning.

Using a repeated classroom rating measure across the treatment period can describe behavior at multiple points within a day, rather than relying on a single assessment. The registry reports least-squares means for the two treatment conditions. The endpoint is therefore a model-based summary, not simply a raw count or a single-time-point score. Details of the model specification beyond the named mixed models analysis are not reported in the registry record.

7. Results Posted in the Registry

• d-Amphetamine Transdermal Patch: mean 12.81 versus 18.67 on control; difference -5.86 (95% CI -6.75 to -4.97), standardized effect d = -1.82; 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.

Onset of Efficacy Measured by Swanson, Kotkin, Agler, M-Flynn, and Pelham (SKAMP) Total Score

• 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:
  • d-Amphetamine Transdermal Patch: mean 12.20 versus 19.00 on control; difference -6.80 (95% CI -9.61 to -3.99), standardized effect d = -0.66; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for d-Amphetamine Transdermal Patch than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Duration of Effect for d-Amphetamine and Placebo Treatment

• 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:
  • d-Amphetamine Transdermal Patch: mean 2.60 versus 1.70 on control; difference 0.90 (95% CI -3.59 to 5.39), standardized effect d = 0.06; z-test p = 0.694.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between d-Amphetamine Transdermal Patch and the control. The interval gives the range of effects that remain compatible with the data.

Change in the Clinician-rated Scale of ADHD Symptoms Based on DSM-IV-TR Criteria (ADHD-RS-IV).

• 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:
  • d-Amphetamine Transdermal Patch: mean -23.40 versus -10.30 on control; difference -13.10 (95% CI -13.38 to -12.82), standardized effect d = -12.84; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for d-Amphetamine Transdermal Patch than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary classroom-behavior question to timing, performance, symptom ratings, parent ratings, and clinical global impression. Taken together, they offer additional views of the study’s outcomes, but they do not all provide the same kind of evidence. Some are repeated or related measures, and some concern different constructs from the primary SKAMP score. Their results should therefore be read as a body of supporting information rather than as interchangeable replications of the primary endpoint.

The registry lists 6 secondary outcomes. Detailed posted summary statistics are available for some of them, while other listed outcomes do not have comparable result entries in the registry record for this record. Where a secondary result has only a recalculated comparison, it is not equivalent to a complete sponsor-reported model result. For the duration outcome, the registry reports a sponsor p-value without the corresponding estimate or confidence interval, while the simple recalculation has a different result. That incomplete reporting limits how much can be inferred from the secondary outcome as a whole.

Secondary outcomes can help assess whether the primary pattern is accompanied by changes in related domains, but their interpretation depends on prespecification, analysis methods, and the number of comparisons considered. If many outcomes or time points are tested, some nominally small p-values can occur by chance even when there is no underlying effect. Adjustments for multiple comparisons or a clear hierarchy of tests can address this concern, but the multiplicity strategy is not reported in the registry record.

Accordingly, unadjusted secondary p-values carry less weight than the registered primary analysis unless the planned testing strategy is known. The secondary findings can be viewed as contextual evidence, but they do not independently settle the primary question or establish broader effects. The record does not report enough detail to determine how secondary testing was prioritized or whether any results were adjusted for multiplicity.

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

• Onset of Efficacy Measured by Swanson, Kotkin, Agler, M-Flynn, and Pelham (SKAMP) Total Score
• Duration of Effect for d-Amphetamine and Placebo Treatment
• Permanent Product Measure of Performance (PERMP) Scores Including PREMP-C and PREMP-A From Different Timepoints Post-dose
• Change in the Clinician-rated Scale of ADHD Symptoms Based on DSM-IV-TR Criteria (ADHD-RS-IV).
• Conners Parent Rating Scale Revised Short Form (CPRS-R:S) Total Scores From Week 6 and Week 7
• Number of Responders Evaluated by Clinical Global Impression (CGI-I) Scale by Treatments From the Double-blind Treatment Period

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a score on a scale, and the registry reports least-squares means. A mean summarizes the center of a set of measurements, while a least-squares mean is a model-based mean adjusted according to the fitted analysis. It need not equal a simple arithmetic average of all observed scores. The registry names a mixed models analysis for the primary comparison, but the model’s full specification, covariates, covariance structure, and missing-data assumptions are not reported in the registry record.

What does the mean difference represent?

The comparison is expressed as the active-treatment mean minus the placebo mean. The reported negative estimate therefore indicates that the active-treatment condition had a lower estimated SKAMP score. Because higher scores on this scale indicate worse impairment, the direction of the difference favors a lower impairment rating on this endpoint, without by itself establishing clinical importance or generalizability. The sponsor reports a least-squares mean difference of -5.87. The registry’s outcome entries also report treatment-specific least-squares means and standard errors.

A standard error describes the estimated sampling variability of an estimate, such as a mean. It is not the spread of individual participants’ scores. The primary arm standard errors are 0.32 and 0.322. Confusing standard errors with standard deviations would lead to an incorrect impression of how much participant-level scores vary. The registry labels the primary outcome’s dispersion as standard error.

How should the confidence interval be read?

A confidence interval gives a range of values compatible with the data and analysis under repeated-sampling assumptions. It conveys uncertainty about the estimated difference, rather than the range of individual outcomes. The sponsor’s 95% interval for the primary mean difference is -6.76 to -4.97. Because the interval is entirely below zero, it is consistent with a negative mean difference under the stated direction of subtraction. The interval does not account for uncertainties that are not represented in the model, such as unreported model choices or unreported selective reporting.

The registry also reports p < 0.001 for the primary sponsor analysis. A p-value evaluates how incompatible the observed data are with a specified null hypothesis, under the analysis assumptions. It is not an effect-size measure, and it does not quantify the probability that the result occurred by chance. Statistical significance should therefore be considered alongside the estimated difference and its interval.

What is the role of a recalculation?

The posted recalculated comparisons use summary statistics to make simple, unadjusted comparisons. For the primary endpoint, that recalculation estimates a mean difference of -5.86 and an interval from -6.75 to -4.97, with p < 0.001. It is not the same as reproducing the sponsor’s mixed models analysis. A summary-statistic calculation cannot recover all aspects of a repeated-measures model or its adjustment choices. The pooled standard deviation used in such calculations is approximate when inferred from reported standard errors; it is not a directly reported participant-level standard deviation.

The effect-size calculation in the posted comparison is standardized by an approximate pooled standard deviation. A standardized difference expresses a mean contrast relative to variability, which can support comparisons across scales, but it depends on the variability estimate and design assumptions. In a crossover study, a simple calculation that treats groups as if they were independent can omit the within-participant pairing and other model features. It should not be treated as the trial’s primary inferential method.

Why does the crossover design matter?

In a crossover design, a participant receives more than one treatment condition, so measurements under different conditions may be related within the same person. That pairing can affect the appropriate variance calculation. A mixed model can account for repeated observations and relevant design structure when specified appropriately. The registry identifies a mixed models analysis for the primary comparison but does not report enough details to assess exactly how sequence, period, or within-person correlation were handled. The simple unadjusted recalculation is consequently best treated as a descriptive cross-check, not as a design-aware substitute.

What does statistical significance establish?

Statistical significance concerns compatibility with a null hypothesis under the chosen model and threshold. It does not establish that a score difference is meaningful to participants, that the result persists beyond the measured period, or that benefits outweigh harms. Clinical interpretation would require context about the scale, meaningful change thresholds, study duration, and outcomes beyond the primary rating. Those thresholds and broader outcome conclusions are not reported in the registry record.

Finally, the trial’s original statistical plan is not reported in the registry record. The description of a mixed models analysis and a reported confidence interval supports interpretation of the posted primary analysis, but it does not reveal all analytic decisions. This matters when considering repeated measurements, crossover structure, endpoint selection, and multiple secondary comparisons.

11. Confidence Intervals and Precision

The primary sponsor estimate is a least-squares mean difference of -5.87, with a 95% confidence interval from -6.76 to -4.97. The interval is relatively concentrated around the estimate and does not include zero. Under the reported model, the data are therefore consistent with a negative treatment contrast across the values in that interval. The interval describes uncertainty in the estimated mean difference; it does not describe the range of scores among individual participants.

The recalculated estimate is -5.86, with a confidence interval from -6.75 to -4.97. Its closeness to the sponsor’s reported estimate is a useful summary-statistic check, but the recalculation is unadjusted and does not reproduce the mixed models analysis. Precision should be judged primarily from the sponsor-reported interval for the primary endpoint, while recognizing that the registry does not give the complete model specification.

Confidence intervals are informative because they show both direction and a range of plausible effect estimates under the analysis assumptions. They do not account for every source of uncertainty. In particular, uncertainty about unreported analytic choices, the selection of outcomes, and generalization beyond the studied population is not fully represented by the interval. Nor does a narrow interval establish that the difference has a particular clinical importance; the record does not report a threshold for a clinically meaningful SKAMP change.

For the primary score, the negative direction is interpretable because higher SKAMP scores indicate worse impairment. The interval’s exclusion of zero supports a statistically distinguishable difference under the sponsor’s model, but the practical meaning still depends on the scale and context. Precision is therefore more than whether an interval excludes zero: its width, assumptions, endpoint meaning, and applicability all matter.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For these continuous outcomes, the figures are participants per arm; the registry’s planning note says that only time-to-event tables would give total event counts. The assumptions for the illustration are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial’s sample-size justification is not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm associated with an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumed analysis conditions held. The 90% power column gives the corresponding planning figure for a 90% chance. Neither column describes what the completed trial actually achieved. These figures are not observed power.

Rows for 100%, 75%, and 50% of the observed effect illustrate how the planned effect size changes the requirement. A smaller effect is harder to distinguish from random variation and therefore requires more participants under the same assumptions. The table and curve should be read as sensitivity illustrations, not as recommendations or as evidence that the original study was adequately or inadequately sized.

These calculations use an unadjusted approximation from posted summary statistics. The trial used a crossover design and the primary sponsor analysis was a mixed models analysis, so the illustrations may not represent the design-specific precision or analysis choices of the actual trial. The registry does not report the original assumptions that informed enrollment.

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 = -5.860; pooled standard deviation σ = 3.218.
2. n = 2 × (1.96 + 0.842)² × 3.218² / -5.860² = 4.7, 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 <- -5.86                      # observed difference in means
sigma <- 3.21817108395874                     # 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(1711021)
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), 7 (90% power)
 75% of observed effect: n per arm = 9 (80% power), 12 (90% power)
 50% of observed effect: n per arm = 19 (80% power), 26 (90% power)
power.t.test: 5.9 
Simulated power at n = 5 per arm: 0.705 (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 analysis is reported as a mixed models analysis of least-squares means. It gives a mean difference of -5.87, a 95% confidence interval from -6.76 to -4.97, and p < 0.001. The posted recalculation from summary statistics gives -5.86, with a confidence interval from -6.75 to -4.97 and p < 0.001. The estimates and intervals are very similar, but the analyses are not identical: the recalculation is unadjusted and does not reproduce the mixed model or its handling of the crossover and repeated measurements.

The recalculation is best understood as a cross-check on the direction and approximate magnitude of the primary comparison. It cannot replace the sponsor’s model-based analysis, which is the analysis reported by the registry for the primary endpoint. The record does not provide the complete model specification needed to independently reconstruct that analysis.

For the secondary duration outcome, the registry reports a sponsor analysis with p = 0.01 but does not report an estimate or confidence interval for that analysis. The summary-statistic recalculation gives a different p-value, 0.694, and a wide interval that includes zero. Since the methods and estimates for the sponsor analysis are not fully reported for this secondary result, the two outputs should not be treated as if they were generated by the same procedure. The registry record does not explain the difference.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when analyses test several outcomes, time points, treatment contrasts, or subgroups. The more tests considered, the greater the chance that at least one will appear statistically notable by chance alone. This is a general statistical issue, not evidence that any specific result in this study is false. It matters because the record lists multiple secondary outcomes and the primary SKAMP measure itself summarizes ratings across several post-dose time points.

The registry record does not report whether the investigators used a multiplicity adjustment, a hierarchy of hypotheses, or another prespecified strategy to control the interpretation of multiple tests. Without that information, nominal secondary p-values should not be interpreted as though each were the only test conducted. The primary endpoint has a designated role in the registry, but the details of any broader testing plan are not reported.

The record defines the primary Full Analysis Set as consented and randomized subjects who took at least one dose of study medication. This definition identifies the intended population for that endpoint, but the registry does not give a full account of exclusions, missing score handling, imputation, or sensitivity analyses. It also does not explain why the analysis counts differ across outcome entries. Those details would help assess whether missingness or analysis-population choices could influence the estimates.

Missing data can affect a repeated-measures analysis if the reason measurements are absent is related to outcomes or treatment. Statistical models can use incomplete observations under assumptions, but those assumptions need to be understood to judge robustness. The registry names a mixed models analysis for the primary result without providing the complete model or missing-data approach. No assumption about the missing-data mechanism should therefore be inferred.

The record also does not report interim analyses, stopping rules, or the original sample-size justification. These matters are distinct from the posted planning illustration, which is based on observed effects and is not the trial’s original design calculation. In sum, the primary result is interpretable as reported, while the unreported analysis-plan details limit independent evaluation of multiplicity and missing-data sensitivity.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry’s safety summaries report serious adverse events and deaths separately for the dose-optimization phase and the double-blind treatment arms. In the dose-optimization group, 0 serious adverse events were reported among 110 at risk, and deaths were 0. In the double-blind d-ATS arm, 0 serious adverse events were reported among 106 at risk, and deaths were 0. In the double-blind placebo arm, 0 serious adverse events were reported among 106 at risk, and deaths were 0.

These are counts recorded for the stated groups and phases. The dose-optimization and double-blind summaries refer to different periods, and the crossover design means the double-blind treatment summaries should not be interpreted as independent parallel-group cohorts. The figures do not establish that no adverse events of any kind occurred: the registry separately reports other adverse events affecting 108 people in dose optimization, 44 in the double-blind d-ATS arm, and 32 in the placebo arm.

Zero recorded serious events in these summaries is a statement about what the registry reports during the specified study periods. It does not establish the absence of risks that are rare, delayed, or not captured in the study. The registry record does not provide further serious-event terms in its summary.

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

The primary result describes a lower mean SKAMP total score in the d-Amphetamine Transdermal Patch condition than in the placebo condition during the double-blind treatment period. The sponsor’s model-based estimate is -5.87, with a 95% confidence interval from -6.76 to -4.97 and p < 0.001. Since higher SKAMP scores indicate worse impairment, the direction corresponds to lower rated classroom-behavior impairment on this particular scale within the study conditions.

That result does not, by itself, establish how much the score difference matters to children, families, or teachers. The registry does not report a threshold for a clinically meaningful SKAMP change. Nor does an average difference imply that every participant had the same response. Group means can conceal individual variation, and the registry’s posted summary does not describe that variation in detail.

The finding also does not establish effects beyond the measured study period, in other settings, or for all children and adolescents with ADHD. The study included a dose optimization phase and a randomized crossover treatment period; the described double-blind population included subjects who reached an optimal dose. The result should be interpreted in that context rather than generalized automatically to people who would not meet the same study conditions.

Statistical significance is not proof of a mechanism, long-term effectiveness, or overall benefit-harm balance. The safety summaries show no serious adverse events or deaths in the stated groups, but they also record other adverse events. The registry does not provide enough information to use these summaries as a complete assessment of uncommon or longer-term harms.

Finally, the primary result is a measure-specific comparison, not a standalone clinical recommendation. It can support a conclusion about the posted SKAMP score contrast under the reported analysis, while leaving questions about clinical importance, broader outcomes, longer follow-up, and generalizability unresolved.

18. Why This Trial Matters Statistically

This trial is statistically instructive because it combines repeated classroom ratings with a crossover design. The primary outcome averages observations at multiple post-dose times, and the same participant may contribute measurements under both treatment conditions. That structure makes the choice of analysis important: observations within a person can be correlated, so a model that accounts for repeated measures may differ from a simple comparison of independent groups.

The registry reports a mixed models analysis for the primary endpoint and provides a model-based least-squares mean difference with a confidence interval. A simple recalculation from the posted summary statistics reaches a very similar estimate, but it cannot reconstruct the full model. Seeing both kinds of result illustrates why a numerical cross-check can be reassuring about direction and broad magnitude while still not replacing an analysis suited to the trial design.

The endpoint also illustrates the distinction between measurement and interpretation. SKAMP uses structured observer ratings of classroom behavior, and its score direction is explicit: higher values indicate worse impairment. A statistically precise difference on a defined scale is useful evidence about that measure, but it does not automatically answer questions about clinical importance or outcomes outside the classroom rating context.

Finally, the registry’s limited reporting of multiplicity, missing-data handling, model details, and original sample-size justification shows why statistical interpretation depends on more than a p-value. The posted primary result is informative, while the limits of the record constrain how fully its assumptions and secondary evidence can be evaluated.

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 does not provide the full statistical analysis plan, detailed mixed-model specification, or complete account of how the crossover structure and repeated measurements were handled. The record also does not report the method used for missing observations, sensitivity analyses, or the rationale for variation in outcome-specific analysis counts. These omissions limit independent assessment of the primary model’s assumptions.

The dose optimization period and eligibility for double-blind treatment are important context. The record says that subjects who reached an optimal dose by the end of dose optimization were randomized to double-blind treatment, but it does not give complete details of how that criterion was defined or how many participants did not proceed. The result may therefore not describe every participant initially enrolled in the same way.

The primary endpoint is a classroom-behavior rating aggregated across multiple daily time points. The registry does not report a clinically meaningful difference threshold or a measure of how the average contrast maps to individual experience. The study’s duration and setting also limit conclusions about longer-term outcomes or behavior outside the laboratory classroom context.

The registry lists several secondary outcomes but does not report a multiplicity strategy. Some secondary sponsor analyses are incomplete in the record, and the recalculations based on summary statistics do not reproduce the sponsor’s model-based procedures. The original sample-size justification is also not reported; the planning illustrations based on observed effects should not be used to infer the original design rationale.

Safety reporting is limited to the posted adverse-event counts and study periods. The absence of reported serious adverse events or deaths in those summaries does not resolve questions about rare or delayed events. These limitations concern the scope and reporting of the evidence, not a claim that any particular analysis or finding is invalid.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate Safety & Efficacy of d-Amphetamine Transdermal System vs Placebo in Children & Adolescents With ADHD — NCT01711021.
• Registry record last updated 2023-12-21; status last verified 2023-12.
• Results first posted 2023-12-21.
• 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 NCT01711021, a completed Phase 2 randomized, triple-masked, placebo-controlled crossover study of d-Amphetamine Transdermal Patch in children and adolescents with ADHD. It reports a 5-week open-label dose optimization period followed by a 2-week randomized double-blind treatment period. The primary endpoint was mean SKAMP total score during the double-blind period, based on ratings across 9 post-dose time points.

The sponsor reports a least-squares mean difference of -5.87 for d-Amphetamine Transdermal Patch versus placebo, with a 95% confidence interval from -6.76 to -4.97 and p < 0.001. Lower SKAMP scores indicate less rated impairment. The posted adverse-event summaries record 0 serious adverse events and 0 deaths in each stated phase or treatment group. Important details—including the full analysis plan, multiplicity strategy, and missing-data methods—are not reported in the registry record.