Safety, Tolerability and Efficacy of SPD503 in Treating ADHD in Children Aged 6-17: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety, Tolerability and Efficacy of SPD503 in Treating ADHD in Children Aged 6-17 (NCT00150592), a randomized phase 2 study. The primary outcome is Change From Baseline in Choice Reaction Time (CRT) at 6 Weeks.

2. Clinical Question

This question concerns performance on a specific computerized attention task over the stated follow-up. It is not identical to asking whether participants improved across every aspect of ADHD, or whether changes in daily functioning were sustained beyond the assessment period. The registry lists additional measures, including rating scales, sleepiness measures and other cognitive tasks, but those outcomes address distinct domains. The primary endpoint therefore provides a focused comparison rather than a complete account of participants’ experience or clinical status.

3. Trial Design

The registry identifies this as a Phase II, randomized, double-masked, parallel-group study of SPD503 compared with placebo. Its stated purpose was to assess the effects of SPD503 on tasks of sustained attention in children and adolescents aged 6-17 diagnosed with ADHD. The study was sponsored by Shire and is listed as completed. The recorded study start was 2005-05-12, and primary completion was 2005-10-05.

Enrollment is listed as 182 participants. That is the registry’s overall enrollment figure; it should not be confused with the numbers contributing to the primary endpoint summaries. For that endpoint, the posted per-protocol group sizes are 80 for SPD503 and 35 for placebo. The registry defines the primary per-protocol population as participants who completed the study and were judged protocol-compliant. Why those analysis counts differ from overall enrollment, and what happened to participants who were not included, are not reported in the registry record.

The primary outcome was change from baseline in CRT at 6 weeks. The registry also lists secondary outcomes covering digital symbol substitution/coding, spatial working memory, ADHD symptom ratings, clinical global improvement and sleepiness. Their presence indicates that the study assessed more than one aspect of performance and participant status; it does not make these outcomes interchangeable with the primary attention-task measure.

The registry record does not report the original sample-size justification, planned allocation ratio, detailed randomization or masking procedures, treatment dose, or a complete statistical analysis plan. It also does not report whether interim analyses were planned or conducted. These omissions limit what can be concluded about the original design decisions, but do not prevent describing the posted endpoint summaries and reported analysis.

4. Participant Flow and Accounting

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

Before assignment: A total of 182 subjects were enrolled. Four (4) subjects were terminated prior to receiving study medication. Thus, 178 were randomized and received study medication.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per protocol (PP) defined as all subjects who completed the study and were deemed to be protocol-compliant.

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 Change From Baseline in Choice Reaction Time (CRT) at 6 Weeks, measured over Baseline and 6 weeks.

The primary endpoint was change from baseline in choice reaction time (CRT) at 6 weeks, measured in msec. CRT is a computerized task in which a participant holds down a press-pad and releases it in response to a yellow dot appearing in one of five screen locations. The time from the stimulus to the response is recorded as reaction time. The task’s stated range is 100 to 5000 msec, and lower scores indicate better performance.

A response-time task provides a direct, standardized way to assess a specific aspect of attention and response speed under the conditions of the test. It can be compared between randomized groups using a continuous outcome, retaining information about the magnitude and variability of the measured response rather than reducing every result to a binary category. This endpoint is relevant to the stated study purpose of assessing sustained attention, although the registry description alone does not establish how closely performance on this task reflects attention or functioning in everyday settings.

The posted group values are mean changes from baseline, with standard deviations describing variability among participants. The primary endpoint population is per protocol, restricted to participants who completed the study and were judged compliant. The registry record does not give further details about the calculation of each participant’s change score, the handling of missing measurements, or any additional adjustments used in the sponsor’s analysis.

7. Results Posted in the Registry

• SPD503: mean 20.70 versus 21.90 on control; difference -1.20 (95% CI -26.53 to 24.13), standardized effect d = -0.02; z-test p = 0.926.

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.

Change From Baseline in Digital Symbol Substitution Task/Coding Test (DSST/Coding) Scores at 6 Weeks in Age Category 8-17 Years

• 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:
  • SPD503: mean 18.30 versus 20.70 on control; difference -2.40 (95% CI -8.97 to 4.17), standardized effect d = -0.16; z-test p = 0.474.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SPD503 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Attention Deficit Hyperactivity Disorder Rating Scale (ADHD-RS-IV) Total Score at 6 Weeks

• 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:
  • SPD503: mean -8.80 versus -5.50 on control; difference -3.30 (95% CI -5.46 to -1.14), standardized effect d = -0.52; z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for SPD503 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Improvement in Clinical Global Impression-Improvement (CGI-I) at 6 Weeks

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • SPD503: 55.4% (67/121) versus 35.1% (20/57) on control; risk difference 20.3 percentage points (95% CI 5.1 to 35.5), risk ratio 1.58 (1.07–2.33); unadjusted two-proportion z-test p = 0.012.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for SPD503 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes across several domains: cognitive-task performance, ADHD symptom ratings, clinician-rated global improvement and sleepiness. The overall pattern is not uniform across those domains. Some posted secondary comparisons have nominal evidence of a group difference, while others do not; that pattern does not match a simple claim that every outcome moved in the same way. These analyses address different measures and populations, so they should not be collapsed into a single summary of benefit or lack of benefit.

The secondary results do not change what the primary CRT comparison estimates. They may provide context about other measured outcomes, but they are not replacements for the prespecified primary question simply because a particular secondary result has a smaller p-value. Differences between outcomes can reflect the fact that each measures a distinct construct, uses its own analysis population, or has different variability and precision.

Multiple outcomes create a multiplicity concern: when many comparisons are examined, the chance of finding at least one apparently unusual result can increase even if no underlying group differences exist. The registry record does not report a multiplicity-adjustment procedure or a hierarchy for interpreting secondary endpoints. Consequently, unadjusted secondary p-values are best treated as exploratory signals rather than as stand-alone confirmation. This caution applies even when a secondary comparison appears more statistically persuasive than the primary outcome.

The secondary measures can help describe the breadth of what was assessed, but the registry record does not supply enough information to determine whether all planned outcomes are posted, whether analyses were selected after results were known, or how missing measurements affected each comparison. The overall secondary pattern should therefore be read alongside the endpoint-specific definitions and analysis details, not as an independent verdict on the primary finding.

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

• Change From Baseline in Digital Symbol Substitution Task/Coding Test (DSST/Coding) Scores at 6 Weeks in Age Category 8-17 Years
• Change From Baseline in DSST/Coding Scores at 6 Weeks in Age Category 6-7 Years
• Change From Baseline in Spatial Working Memory (SWM) Scores at 6 Weeks
• Change From Baseline in Attention Deficit Hyperactivity Disorder Rating Scale (ADHD-RS-IV) Total Score at 6 Weeks
• Number of Participants With Improvement in Clinical Global Impression-Improvement (CGI-I) at 6 Weeks
• Change From Baseline in Pediatric Daytime Sleepiness Scale (PDSS) Scores at 6 Weeks
• Change From Baseline in Pictorial Sleepiness Scale (PSS) Scores at 6 Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference describe?

The primary measure is continuous, so the comparison can be expressed as a difference between the groups’ mean changes. The posted recalculation subtracts the placebo mean change from the SPD503 mean change. Its estimate is -1.2 msec. This gives a direction and magnitude on the original measurement scale: it is not a percentage change, a treatment-response rate, or an adjusted estimate. A mean difference compresses the group distributions into a single contrast, so it should be read together with the standard deviations and confidence interval rather than as a description of every participant’s result.

The standard deviation describes how dispersed participant measurements are around a group mean. The posted standard deviations for the primary outcome are 63.11 msec in the SPD503 group and 64.04 msec in the placebo group. A large spread relative to the mean difference makes the group contrast harder to estimate precisely. General statistical principle: when observations vary substantially, the same average contrast is typically estimated with less precision unless there is enough information to offset that variability.

What does the confidence interval add?

The 95% confidence interval for the recalculated unadjusted mean difference extends from -26.53 to 24.13 msec. A confidence interval is a range of values compatible with the observed data under the method’s assumptions. In repeated use of the same procedure, intervals constructed this way would cover the fixed underlying quantity at the stated rate. It is not a range containing a known proportion of individual participants, nor does it assign a probability to the true value after the data have been observed.

Because the interval crosses zero, the data are compatible with an unadjusted mean difference in either direction, as well as with no difference. Its width also conveys limited precision: the estimate does not pin down a narrow range of plausible group contrasts. A confidence interval does not establish whether any value within it would be important to participants; the registry record does not report a threshold for a meaningful CRT difference.

How should the p-values be read?

The unadjusted recalculation reports p = 0.926. A p-value describes how unusual data at least as incompatible with the null comparison would be under a specified statistical model if the null hypothesis were true. It is not the probability that the null is true, the probability that results occurred by chance, or a measure of the size of the effect. A large p-value does not prove that groups are equivalent. Here it accompanies an estimate near zero and a broad interval that permits differences in either direction.

The registry separately reports an ANCOVA p-value of 0.844. ANCOVA is a regression-based method that compares outcome values while accounting for specified covariates, often including a baseline measure. The registry does not identify the covariates or provide the adjusted contrast and its confidence interval. Therefore, the reported p-value can be stated, but the adjusted magnitude and precision cannot be reconstructed from the record. The unadjusted and ANCOVA p-values should not be treated as duplicate calculations of precisely the same estimand.

What does the analysis population mean?

The primary outcome is reported for a per-protocol population, defined in the registry as participants who completed the study and were deemed protocol-compliant. Such an analysis describes the participants meeting those conditions, rather than automatically representing every randomized participant. The reasons for exclusion, numbers excluded by group, and consequences of exclusions are not reported in the registry record. The registry does not provide enough detail to assess whether exclusions could have affected comparability between randomized groups.

The posted primary group sizes are 80 and 35, while overall enrollment is 182. Those figures refer to different populations and should not be read as contradictory counts. The difference between overall enrollment and the primary analysis counts signals that the primary results are based on a subset, but the record does not explain the full participant flow.

Why are planning calculations not trial results?

Planning illustrations use the observed effect as a reference and calculate hypothetical participant requirements under stated assumptions. For these illustrations, the assumptions are a two-sided significance level of 0.05, equal allocation between arms, a normal approximation, and an effect set to a stated fraction of the observed effect. The figures for continuous outcomes are participants per arm. They describe possible future planning scenarios, not participants actually analyzed and not evidence about the probability that this completed trial detected an effect.

General statistical principle: planning requirements increase as the effect to detect becomes smaller, because a smaller contrast is harder to distinguish from random variation. The posted calculations are sensitive to the observed effect used as their starting point. If that estimate is uncertain, the resulting planning figures are uncertain too. The registry record does not report the assumptions or justification used for the original trial design, so these illustrations should not be presented as that original rationale.

General statistical principle: over-dispersion matters when observed variability is greater than a model assumes, because standard errors may be understated and confidence intervals too narrow if the model does not accommodate it. The primary outcome is reported as a continuous mean with standard deviations, and the record does not identify an over-dispersion assessment. This general issue should not be mistaken for a reported finding about this trial.

11. Confidence Intervals and Precision

The recalculated primary mean difference is -1.2 msec, with a 95% confidence interval from -26.53 to 24.13. That interval includes zero and extends in both directions. It indicates that the observed data do not estimate the group contrast precisely enough to distinguish a small estimate from a range of materially different contrasts. The direction of the point estimate alone is therefore not a secure basis for interpreting the result.

The group standard deviations, 63.11 msec for SPD503 and 64.04 msec for placebo, show that individual change scores varied considerably around the group means. Variation among individuals and precision of the group contrast are related but not identical: precision also depends on how many participants contribute to the analysis. The primary summaries use 80 participants in the SPD503 group and 35 in the placebo group. The unequal analysis counts are relevant context when reading the interval, but the registry record does not report why they differ.

The confidence interval is for the recalculated unadjusted comparison. The sponsor-reported ANCOVA result is a p-value without a posted adjusted estimate or interval. Its precision therefore cannot be evaluated directly from the reported ANCOVA fields. The sponsor’s analysis should be distinguished from the unadjusted calculation rather than treating the unadjusted interval as if it were the ANCOVA interval.

Precision is not the same as clinical importance. The registry describes the task and scoring direction, but does not report a threshold for a meaningful difference in CRT. As a result, the interval can be interpreted statistically, but the record does not establish which values within it would matter in practice. It also does not establish equivalence: demonstrating equivalence would require an appropriate margin and analysis, neither of which is reported in the registry record.

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 participants and not total events. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. Time-to-event planning displays, when applicable, count total events using the Schoenfeld method; that is not the basis for these continuous-outcome figures.

The 80% power column describes a hypothetical design’s chance of detecting an effect of the specified size under the planning assumptions, if that effect and model assumptions were correct. The 90% power column uses a higher target chance of detection and therefore generally requires more participants for the same effect. These are design targets, not probabilities that the observed result is true or that the treatment has a particular effect.

Each scenario scales the observed effect to a stated fraction. Planning for 75% of the observed effect or 50% of the observed effect means planning to detect a smaller contrast than the full observed estimate. Smaller effects are harder to distinguish from random variation, so they require more participants under otherwise similar assumptions.

These figures are planning illustrations based on the observed effect, not observed power. They are not a reconstruction of the trial’s original design justification. The original sample-size assumptions and justification are not reported in the registry record. Because the observed primary estimate is imprecise, planning from it should also be viewed as uncertain; the illustrations do not establish that the original trial was adequately or inadequately sized.

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 = -1.200; pooled standard deviation σ = 63.391.
2. n = 2 × (1.96 + 0.842)² × 63.391² / -1.200² = 43,806.0, rounded up to 43,807 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 <- -1.2                      # observed difference in means
sigma <- 63.3912580374867                     # 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(150592)
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 = 43,807 (80% power), 58,644 (90% power)
 75% of observed effect: n per arm = 77,878 (80% power), 104,256 (90% power)
 50% of observed effect: n per arm = 175,225 (80% power), 234,576 (90% power)
power.t.test: 43807 
Simulated power at n = 43,807 per arm: 0.803 (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 reports the sponsor’s primary comparison as an ANCOVA analysis with p = 0.844. It does not post an adjusted mean difference or confidence interval for that analysis. ANCOVA can account for covariates specified in the analysis, but the registry record does not identify which covariates were included. The adjusted effect’s direction, magnitude and precision therefore cannot be described from the reported ANCOVA result alone.

The recalculation is a simple unadjusted comparison of the posted group summaries. It gives a mean difference of -1.2 msec, a 95% confidence interval from -26.53 to 24.13, and p = 0.926. These statistics are not the sponsor’s ANCOVA estimates. The p-values differ because the methods and information used in the comparisons may differ; the registry record does not provide enough detail to attribute the difference to a particular adjustment.

There is no reported discrepancy between the sponsor analysis and the recalculation requiring the recalculation to take precedence. The sponsor’s own ANCOVA analysis therefore takes precedence as the reported trial analysis. The unadjusted calculation remains useful as a transparent description derived from posted summaries, but it should not be represented as the trial’s adjusted primary estimate. Since the sponsor’s adjusted contrast and interval are not posted, the unadjusted confidence interval should not be used to imply a level of precision for the ANCOVA result.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes and reports analyses for them, in addition to the primary endpoint. It does not report a multiplicity-control procedure, such as an adjustment to the significance threshold, or a prespecified hierarchy for testing the outcomes. When multiple hypotheses are tested, the chance of at least one nominally notable result can increase. This is a general statistical concern, not evidence that any particular posted result is false. Without a reported strategy, secondary p-values should be interpreted as nominal and with caution.

The record does not report whether the primary endpoint was designated as the sole confirmatory test or how secondary outcomes were intended to support interpretation. The existence of a primary endpoint and a list of secondary outcomes is not enough to infer the complete testing plan. Interim analyses, stopping rules, subgroup plans and any adjustment for repeated looks are not reported in the registry record.

The primary analysis is per protocol, defined as participants who completed the study and were deemed protocol-compliant. The registry does not report a participant-flow account explaining exclusions or the numbers excluded from each group. It also does not report whether an intention-to-treat analysis was performed, how missing outcomes were handled, whether values were imputed, or whether sensitivity analyses assessed the consequences of missing data. The posted group counts alone cannot answer those questions.

Missing outcomes can affect both the analysis population and the balance created by randomization, especially if missingness is related to participants’ outcomes or group assignment. This is a general consideration; the registry record does not state that such a problem occurred. Similarly, the record does not provide enough detail to assess protocol deviations, outcome-measure reliability or the completeness of reporting for every planned analysis. These omissions limit the ability to reconstruct the full analysis process, rather than changing the numerical results that are posted.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: asthma exacerbation (0.8%), moderate loss of consciousness (0.8%).

For serious adverse events, the registry lists 2 affected participants among 121 at risk in the SPD503 group and 0 among 57 at risk in the placebo group. The serious-event terms listed are asthma exacerbation and moderate loss of consciousness, each reported as 0.8%. The registry does not specify in this summary how those terms map to individual participants or provide further event-level detail, so the terms should not be interpreted as a complete account of severity, timing or relatedness.

The at-risk counts differ from the primary per-protocol endpoint counts. They refer to the posted safety groups and should not be substituted for the primary analysis population. The registry also lists other adverse events, but these are distinct from the serious adverse event counts. Deaths are not reported in the registry record.

These figures describe the events recorded in this study; they do not by themselves establish that an event was caused by treatment or quantify comparative risk with precision. The registry record does not report the adjudication, attribution or follow-up details needed for a fuller safety assessment. The small number of serious events also means that these counts alone provide limited information about uncommon outcomes.

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

The posted primary data show similar average changes in CRT between the SPD503 and placebo groups, with a recalculated unadjusted difference of -1.2 msec. The 95% confidence interval, from -26.53 to 24.13, includes zero and extends in both directions. The sponsor-reported ANCOVA p-value is 0.844, but the adjusted estimate and confidence interval are not posted. Taken together, the record does not provide a precise estimate of a primary-outcome difference.

This is not proof that the groups were equivalent, nor does it establish that the underlying effect is exactly zero. A result that does not clearly distinguish the groups can arise when the actual contrast is small, when the estimate is imprecise, or both. The registry record does not report an equivalence margin, so equivalence cannot be inferred from the primary result.

The finding is confined to a specific measure, population and follow-up: change in a computerized choice reaction time task at 6 weeks among participants included in the per-protocol primary analysis. It does not automatically generalize to all enrolled participants, other ages, other clinical settings, other ADHD outcomes or longer-term effects. The study also includes secondary measures, but those do not alter the definition of the primary question and their interpretation is limited by the lack of reported multiplicity methods.

The record supports describing the posted measurements and their uncertainty, not making medical recommendations. It does not establish how a particular participant should be treated or whether an individual will experience a particular outcome. The primary endpoint is a task-based measure, and the registry does not report a threshold translating its change into a meaningful difference in everyday functioning. The appropriate statistical conclusion is therefore bounded: the primary estimate is close to zero, but its uncertainty leaves a range of possible contrasts unresolved.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate and its uncertainty need to be read together. The recalculated primary contrast is close to zero, but the confidence interval spans values on either side of zero. Looking only at the point estimate could make the result appear more definitive than it is; looking only at a p-value would conceal the range of contrasts compatible with the data.

The record also distinguishes a sponsor-reported adjusted analysis from a simple unadjusted recalculation. The ANCOVA p-value is reported, but the adjusted effect estimate and interval are not. This makes it possible to identify the sponsor’s analytic method and reported test result, while limiting direct assessment of the adjusted effect’s magnitude and precision. Transparent reporting of estimates and intervals alongside p-values is useful for understanding what a trial has and has not resolved.

Analysis populations matter as well. Overall enrollment is 182, whereas the primary per-protocol summaries include 80 and 35 participants in the two groups. The registry defines who counts as per protocol but does not explain the full flow from enrollment to analysis. That gap is important because results from a compliant completer subset answer a narrower question than results for all randomized participants.

Finally, the range of secondary outcomes demonstrates the interpretive challenge of testing multiple measures. Findings across distinct cognitive, symptom, global-improvement and sleepiness domains may not align. Without a reported multiplicity strategy, isolated secondary signals warrant less confidence than a prespecified and appropriately controlled primary analysis. These statistical considerations help readers distinguish what the posted record estimates from what remains uncertain.

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 primary endpoint is reported for a per-protocol population rather than a clearly documented analysis of all randomized participants. Although the registry defines that population, it does not explain why the analysis counts differ from overall enrollment or provide a complete accounting of exclusions by group. This limits assessment of how selection into the analysis may affect interpretation.

The sponsor’s primary ANCOVA result is reported only as a p-value. The adjusted contrast, confidence interval, covariates and model details are not reported in the registry record. The recalculated unadjusted estimate is therefore not a substitute for a full report of the sponsor’s analysis. The primary endpoint’s unadjusted confidence interval is broad, leaving the direction and magnitude of the underlying contrast uncertain.

The record does not report the original sample-size justification, detailed randomization or masking procedures, treatment dosing, missing-data methods, interim analyses or the complete statistical analysis plan. It also does not report a threshold for a meaningful CRT change, making it difficult to connect statistical differences to practical importance. The study’s stated follow-up for the primary outcome is 6 weeks, so the result does not describe later outcomes.

There are multiple secondary measures, but a multiplicity adjustment or testing hierarchy is not reported. Their nominal results therefore require caution. The safety summary provides limited event information and does not report deaths; it does not provide enough detail to assess event timing, attribution or the full context of safety monitoring. These are limitations of the registry record, and do not establish that the trial lacked procedures or analyses that were simply not reported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety, Tolerability and Efficacy of SPD503 in Treating ADHD in Children Aged 6-17 — NCT00150592.
• Registry record last updated 2021-06-10; status last verified 2021-05.
• Results first posted 2009-10-14.
• 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

NCT00150592 is a completed Phase II, randomized, double-masked, parallel-group study sponsored by Shire. It compared SPD503, identified as guanfacine HCl, with placebo in children and adolescents aged 6-17 with ADHD. Overall enrollment is listed as 182.

The primary outcome was change from baseline in choice reaction time at 6 weeks, measured in msec, with lower scores indicating better performance. The primary result is reported for a per-protocol population. The unadjusted recalculation estimates a mean difference of -1.2 msec, with a 95% confidence interval from -26.53 to 24.13; the sponsor-reported ANCOVA p-value is 0.844.

The registry lists secondary cognitive, symptom, global-improvement and sleepiness outcomes. It does not report the original sample-size justification, multiplicity strategy, missing-data methods or a complete adjusted primary estimate. The posted primary comparison is imprecise and does not establish a clear difference between groups on the CRT measure.