Efficacy and Safety of Armodafinil as Adjunctive Therapy in Schizophrenic Adults With Cognitive Deficits: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Armodafinil as Adjunctive Therapy in Schizophrenic Adults With Cognitive Deficits (NCT00487942), a randomized phase 2 study. The primary outcome is Mean Change From Baseline to Last Observation After Baseline in Composite Score on the Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery.

2. Clinical Question

The trial was designed to evaluate cognitive change during a short treatment period. The primary outcome focuses on a composite score rather than a single test: it brings together scores from the battery’s cognitive assessments into a summary measure. The registry describes the score as a normative T-score, with a reference mean of 50 and standard deviation of 10. The posted outcome is the change from baseline, not the endpoint score alone.

The treatment comparisons concern three separate armodafinil dosage groups, each compared with placebo. The registry lists a 4-week study and specifies that the primary outcome uses the last observation after baseline when available. Secondary outcomes include the composite score at Week 4 and scores in cognitive domains. These outcomes can add context, but the primary question remains the comparison of mean composite-score change across the randomized groups.

3. Trial Design

This was a randomized, double-blind, parallel-group, fixed-dosage Phase 2 study. The registry lists an enrollment of 60 and identifies schizophrenia as the condition. The study title describes adults with cognitive deficits associated with schizophrenia and armodafinil as adjunctive therapy. The sponsor was Cephalon. The registry lists the study start as 2007-07, primary completion as 2007-12, and status as completed.

Participants were assigned to armodafinil 50 mg/day, 100 mg/day, or 200 mg/day, or to placebo. The registry describes a 4-week double-blind treatment period and administration in the morning. The study was placebo-controlled, and the double-blind designation means that treatment assignment was masked as described in the record. The allocation ratio and the details of the randomization procedure are not reported in the registry record.

The primary outcome analysis population was defined as participants who received at least one dose of study drug and had at least one MATRICS efficacy assessment after baseline. The record says that summary statistics are based on observed data. It also says a composite score was treated as missing if any part of that score was missing. These definitions matter: the arm sizes used in the primary outcome summaries are analysis counts and are not necessarily identical to the registry’s enrollment figure.

The record lists multiple outcome measures and analyses, including the primary cognitive composite and secondary cognitive outcomes. It does not report the original sample-size justification, the intended allocation ratio, or a complete statistical analysis plan. Details about interim analyses, if any, are not reported in the registry record. The posted results therefore allow interpretation of the described outcome summaries and analyses, but do not establish every design decision made before the study began.

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 a screening period of at least 1 week, a 4 week double blind treatment period, and a 1 week follow up period. Of the 60 patients enrolled, 59 patients received at least 1 dose of study drug and were evaluated for safety; 1 patient who was assigned to receive placebo withdrew before taking any study drug.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set defined as subjects who received one or more doses of the study drug and who had at least 1 MATRICS efficacy assessment after baseline. If any part of the composite score was missing then the composite score was set to missing. Summary statistics are provided for the observed data only, missing data was not estimated.

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 Mean Change From Baseline to Last Observation After Baseline in Composite Score on the Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery, measured over Baseline and 4 weeks (or last observation after Baseline).

The primary endpoint was mean change from baseline to the last observation after baseline in the MATRICS Consensus Cognitive Battery composite score. The registry describes the battery as containing 10 tests across 7 cognitive domains: speed of processing, attention/vigilance, working memory, verbal learning, visual learning, reasoning and problem solving, and social cognition. The composite combines individual test scores and expresses them on a normative T-score scale. The record states that the composite-score reference mean is 50 and its standard deviation is 10.

Using a composite can summarize performance across several cognitive areas in a single outcome, which corresponds to the study’s stated objective of evaluating cognitive deficits rather than focusing on only one domain. A change-from-baseline outcome compares each participant’s later score with their baseline score; the group mean then summarizes the average observed change. This outcome does not, by itself, show whether every participant changed in the same direction or whether the average reflects a uniform response.

The endpoint timeframe is baseline and 4 weeks, or the last observation after baseline. Thus the primary summary may include a last post-baseline observation rather than a Week 4 measurement for every participant. The registry specifies observed-data summaries and says that a composite score was set to missing if any part of it was missing. The precise handling of missing observations beyond those statements is not reported in the registry record.

7. Results Posted in the Registry

• Armodafinil 50 mg/Day: mean 1.90 versus 2.20 on control; difference -0.30 (95% CI -4.66 to 4.06), standardized effect d = -0.05; z-test p = 0.893.
• Armodafinil 100 mg/Day: mean 2.80 versus 2.20 on control; difference 0.60 (95% CI -4.54 to 5.74), standardized effect d = 0.09; z-test p = 0.819.
• Armodafinil 200 mg/Day: mean 2.90 versus 2.20 on control; difference 0.70 (95% CI -3.22 to 4.62), standardized effect d = 0.14; z-test p = 0.726.

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 to Week 4 in Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery Composite 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 deviations.
• Result:
  • Armodafinil 50 mg/Day: mean 2.20 versus 2.10 on control; difference 0.10 (95% CI -4.60 to 4.80), standardized effect d = 0.02; z-test p = 0.967.
  • Armodafinil 100 mg/Day: mean 3.90 versus 2.10 on control; difference 1.80 (95% CI -2.83 to 6.43), standardized effect d = 0.32; z-test p = 0.446.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Armodafinil 50 mg/Day and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Armodafinil 100 mg/Day and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to Week 4 or Last Observation After Baseline in the Speed of Processing Domain of the Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery

• 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:
  • Armodafinil 50 mg/Day: mean 3.00 versus 0.90 on control; difference 2.10 (95% CI -3.86 to 8.06), standardized effect d = 0.26; z-test p = 0.490.
  • Armodafinil 100 mg/Day: mean 0.00 versus 0.90 on control; difference -0.90 (95% CI -7.54 to 5.74), standardized effect d = -0.10; z-test p = 0.790.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Armodafinil 50 mg/Day and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Armodafinil 100 mg/Day and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to Week 4 or Last Observation After Baseline in the Attention/Vigilance Domain of the Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery

• 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:
  • Armodafinil 50 mg/Day: mean 0.40 versus 3.00 on control; difference -2.60 (95% CI -9.33 to 4.13), standardized effect d = -0.29; z-test p = 0.449.
  • Armodafinil 100 mg/Day: mean 3.70 versus 3.00 on control; difference 0.70 (95% CI -3.79 to 5.19), standardized effect d = 0.12; z-test p = 0.760.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Armodafinil 50 mg/Day and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Armodafinil 100 mg/Day and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover the MATRICS composite at Week 4 and cognitive-domain scores, including speed of processing and attention/vigilance. Across the posted continuous summaries, results vary by domain and dosage, rather than forming a uniform pattern of larger changes across every armodafinil group. The Week 4 composite estimates also do not provide a clear, precise separation from placebo. This broad pattern is consistent with the primary result’s uncertainty, rather than offering a decisive independent resolution of it.

Secondary outcomes can help assess whether a primary composite result is accompanied by changes in specific parts of the cognitive battery or under a different stated timeframe. A domain measure may respond differently from the composite, which combines several tests and domains. Such differences can be informative, but they can also arise from random variation, especially when many outcomes and comparisons are considered.

The registry lists 78 posted secondary outcomes, alongside the primary outcome and other analyses. The record does not report a multiplicity adjustment or a hierarchy specifying how secondary results were to be interpreted. Without that information, individual secondary estimates should be treated as exploratory context rather than as a set of confirmatory tests. Examining many outcomes increases the chance that some estimates will appear favorable or unfavorable by chance alone. The secondary pattern therefore does not replace the primary comparison, and it should not be used to select a dosage based on the most favorable isolated estimate.

The posted summaries also do not provide the same degree of information for every secondary outcome. Not every listed secondary outcome has a recalculated comparison in the record, and the total number of analyses is not itself evidence of consistency. A cautious reading gives more weight to the prespecified primary outcome and considers the secondary outcomes as supporting context, while recognizing that the protocol’s outcome hierarchy and multiplicity procedures are not reported in the registry record.

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

• Change From Baseline to Week 4 in Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery Composite Score
• Change From Baseline to Week 4 or Last Observation After Baseline in the Speed of Processing Domain of the Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery
• Change From Baseline to Week 4 or Last Observation After Baseline in the Attention/Vigilance Domain of the Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery
• Change From Baseline to Week 4 or Last Observation After Baseline in the Working Memory Domain of the Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery
• Change From Baseline to Week 4 or Last Observation After Baseline in the Verbal Learning Domain of the Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery
• Change From Baseline to Week 4 or Last Observation After Baseline in the Visual Learning Domain of the Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery
• Change From Baseline to Week 4 or Last Observation After Baseline in the Reasoning and Problem Solving Domain of the Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery
• Change From Baseline to Week 4 or Last Observation After Baseline in the Social Cognition Domain of the Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) Consensus Cognitive Battery

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a score change measured on a scale. For such outcomes, the mean describes the average change within a group, while the standard deviation describes how spread out individual changes are around that mean. A mean difference compares the average changes in two groups. The recalculated comparisons subtract the placebo mean change from the mean change in each armodafinil group, as represented in the posted estimates; they are unadjusted summaries based on the reported group statistics.

What does an unadjusted comparison tell us?

An unadjusted comparison contrasts the group summaries without accounting for other variables through a regression model. Randomization is intended to make treatment groups comparable on average, but in a study with small analysis groups, chance differences in baseline characteristics can remain. An adjusted model can account for specified covariates, but the registry’s complete model specification is not reported. The posted recalculation is therefore useful as a transparent summary of the observed means, but it does not replace the sponsor’s reported analysis.

The registry reports ANCOVA for the primary comparison. In general, analysis of covariance models an outcome while adjusting for one or more covariates; for a baseline-to-follow-up outcome, baseline score is commonly relevant, but the exact covariates used in this trial are not reported in the registry record. The sponsor’s estimates are reported as effect sizes, so their scale differs from the recalculated mean differences expressed in composite-score units. The registry does not report a p-value for these ANCOVA results.

What do the confidence intervals represent?

In general, a confidence interval describes the range of estimates compatible with the data and the statistical procedure, under its assumptions. It reflects sampling uncertainty and is not a range that contains a fixed proportion of individual participants’ outcomes. A wider interval indicates less precision. An interval that includes zero does not demonstrate that the true difference is zero; it indicates that zero is among the values not ruled out by the interval at that confidence level.

The recalculated intervals are 95% intervals for unadjusted mean differences. The registry’s reported analyses give 95% intervals for ANCOVA effect sizes. Because the estimands differ, the intervals should be interpreted on their respective scales, not compared as though they were two versions of the same numerical estimate. The uncertainty is substantial in both sets of comparisons.

Why report standard deviations?

In general, the standard deviation helps describe how variable individual outcomes are within a group. A mean difference can be small relative to the spread of individual scores, making the group-level estimate difficult to pin down. The posted standard deviations for the primary outcome range across the four groups, and the number contributing to each summary also affects precision. These summaries do not reveal the shape of the score distributions, the presence of outliers, or how paired baseline and follow-up values are related.

For the recalculated comparisons, the standard errors and pooled standard deviations are calculated from the posted summary statistics. The standardized effect size expresses a difference relative to a measure of variability, allowing the magnitude to be described on a scale less dependent on the original score units. Standardization does not remove uncertainty, and a standardized estimate remains sensitive to the variability in the study population. The registry’s ANCOVA effect size and the simple recalculated standardized effect size need not be numerically identical, because their methods and adjustment may differ.

How should the p-values be read?

In general, a p-value measures how incompatible the observed data are with a specified null hypothesis, under the statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The recalculated p-values are explicitly unadjusted. They should be read alongside the estimated differences and intervals, not as stand-alone verdicts. The record does not report p-values for the sponsor’s ANCOVA primary analyses.

There are multiple treatment comparisons and many outcome measures in the registry. When many hypotheses are examined, some estimates may appear more extreme by chance even when there are no corresponding effects. Whether and how the sponsor controlled multiplicity is not reported in the registry record. For that reason, isolated secondary p-values, where available, would require particular caution; the posted secondary summaries do not provide a complete multiplicity-adjusted interpretation.

What limits interpretation of the analysis?

The primary analysis set requires at least one dose and at least one post-baseline assessment, so it is not described as an analysis of every randomized participant regardless of follow-up. The record states that observed data are summarized and that a composite is missing if any component is missing. The method for handling missing outcomes beyond this rule is not reported in the registry record. If missingness is related to participants’ outcomes or treatment experience, an observed-data summary can differ from a summary that would have been obtained with complete follow-up.

The registry also lists a Week 4 composite outcome and several cognitive-domain outcomes. Multiple outcomes can offer a broader view, but they do not all carry the same evidential weight as the prespecified primary endpoint. The original statistical plan, including any hierarchy of outcomes, is not reported in the registry record. General statistical considerations explain why adjustment, missing-data assumptions, and multiplicity matter; they do not establish which choices were made for this trial.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a treatment contrast. The recalculated primary mean-difference intervals are broad: for 50 mg/day, -4.659 to 4.059; for 100 mg/day, -4.536 to 5.736; and for 200 mg/day, -3.217 to 4.617. Each includes zero. Thus the data are compatible with no mean difference and with effects on either side of zero. The intervals do not support a sharply determined estimate for any of the three dosage comparisons.

The registry’s ANCOVA effect-size intervals are also broad: -0.81 to 0.73 for 50 mg/day, -0.68 to 0.86 for 100 mg/day, and -0.66 to 0.95 for 200 mg/day. Those intervals are on the reported effect-size scale, rather than the score-unit scale of the recalculated mean differences. Each includes zero, and each allows a range of effects in both directions. They therefore do not resolve the direction or magnitude of the effect with precision.

A confidence interval is not a guarantee that the true effect lies within its endpoints, nor does it describe the spread of individual participant outcomes. In general, it summarizes uncertainty in an estimate under the method’s assumptions. The analysis group sizes and the observed variability contribute to the breadth of these intervals. The registry’s primary outcome analysis uses observed data, and the handling of missing data beyond the stated composite rule is not reported in the registry record; that adds a further interpretive limitation not captured by the interval alone.

Imprecision cuts both ways. The estimates do not establish a meaningful advantage for an armodafinil dosage, but the intervals also do not rule out all potentially relevant effects. A non-significant unadjusted comparison is not proof of equivalence. More precise conclusions would require evidence that narrows the plausible range, together with a prespecified threshold for what difference would matter. Such a threshold is not 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 sample-size illustrations are planning calculations, not the number of participants observed in the trial. For these continuous outcomes, the entries are participants per arm, not total events. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative participants per arm for a design with an 80% probability of detecting the selected effect under the listed assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding number for a design with a 90% probability under those same assumptions. Higher planned power generally calls for more participants when other assumptions stay the same. The listed quantities are per arm, so they describe the planned size of each compared group, not the overall number enrolled.

Rows for 100%, 75%, and 50% of the observed effect explore what happens if a future study aims to detect a smaller effect than the one estimated in this trial. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the calculation assumptions. The observed effect is estimated from a small study and is uncertain; using it as the basis for planning can produce unstable illustrations, especially when the estimated difference is close to zero.

These figures are not observed power. They do not tell how likely the completed trial was to detect an effect after its results were known, and they are not the trial’s actual enrollment target rationale. They are conditional planning illustrations based on the stated calculation assumptions and observed estimates. The table and curve should therefore be read as sensitivity aids: they show how planned sample size changes with the target effect and power level, not as evidence about the validity of the original design.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.300; pooled standard deviation σ = 5.670.
2. n = 2 × (1.96 + 0.842)² × 5.670² / -0.300² = 5,606.9, rounded up to 5,607 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.3                      # observed difference in means
sigma <- 5.66974426231025                     # 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(487942)
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 = 5,607 (80% power), 7,507 (90% power)
 75% of observed effect: n per arm = 9,968 (80% power), 13,345 (90% power)
 50% of observed effect: n per arm = 22,428 (80% power), 30,025 (90% power)
power.t.test: 5607.9 
Simulated power at n = 5,607 per arm: 0.798 (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 primary analysis reports ANCOVA effect sizes and 95% confidence intervals for each armodafinil dosage versus placebo. The recalculated comparisons instead give simple, unadjusted mean differences in composite-score units, confidence intervals, and unadjusted p-values. These are different analyses and different effect scales, so exact numerical agreement is not expected.

For the reported ANCOVA results, the effect sizes are -0.04 for 50 mg/day, 0.09 for 100 mg/day, and 0.15 for 200 mg/day. The corresponding 95% intervals are -0.81 to 0.73, -0.68 to 0.86, and -0.66 to 0.95. The registry does not report p-values for these analyses. The unadjusted recalculations give mean differences of -0.3, 0.6, and 0.7, respectively, and all three recalculated intervals include zero.

No discrepancy is flagged between the posted results and the recalculation. The sponsor’s reported ANCOVA analyses remain the principal reported analyses; the recalculation is a supplementary way to inspect the arm means and the uncertainty implied by the summary statistics. It should not be presented as an alternative sponsor analysis or as an adjustment for covariates. The registry does not provide enough detail to reconstruct the ANCOVA model, including its full covariate specification.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when analyses test several treatment comparisons, outcomes, timeframes, or subgroups. Even if each analysis uses a conventional significance threshold, looking across many tests raises the chance that at least one result appears unusually strong by chance. The registry lists several primary and secondary cognitive outcomes, along with numerous analyses. The record does not report whether multiplicity was controlled, which outcomes were in a testing hierarchy, or whether secondary comparisons were intended to be confirmatory. Their statistical interpretation should therefore be cautious, particularly if a result is considered in isolation.

The primary analysis population is described as participants who received one or more doses and had at least one MATRICS efficacy assessment after baseline. The record states that summary statistics are based on observed data. It also states that if any component of the composite score was missing, the composite score was set to missing. This is the reported rule for constructing the composite when components are unavailable; it does not fully describe how missing follow-up outcomes were handled in the analysis.

Details such as the amount and reason for missingness by group, assumptions about missing outcomes, imputation methods, and sensitivity analyses are not reported in the registry record. Nor does the record specify whether the primary analysis followed an intention-to-treat estimand or how participants without post-baseline assessments were incorporated. Because the posted analysis set requires a post-baseline assessment, the summary does not necessarily represent every randomized participant.

In general, missing-data methods rely on assumptions about why observations are absent and how absent outcomes relate to observed information. Different assumptions can change estimates, particularly if missingness differs across groups or depends on unobserved outcomes. The registry’s description is not enough to judge the plausibility of those assumptions. These limitations do not invalidate the posted summaries, but they constrain how broadly the results can be interpreted.

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 4% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: psychotic disorder (7.1%).

The registry reports serious adverse events affecting 0 participants in the 50 mg/day group, 0 in the 100 mg/day group, 0 in the 200 mg/day group, and 1 in the placebo group. The corresponding numbers at risk in the safety summaries are 15, 15, 15, and 14. These counts describe participants with serious adverse events as posted; they do not identify the overall likelihood of harm beyond the trial’s observation period, nor do they establish that the observed event was caused by treatment.

The record lists psychotic disorder as a top serious-event term at 7.1%. It does not identify the treatment group for that term in the information, so the percentage should not be assigned to a particular dosage group. Death counts are not reported in the registry record. The numbers of participants with other reported adverse events are 8, 6, 8, and 7 across the 50 mg/day, 100 mg/day, 200 mg/day, and placebo groups, respectively. These summaries are descriptive and do not replace a detailed assessment of event type, timing, severity, or attribution.

Safety counts are based on the registry’s stated at-risk groups, which are not identical to the primary outcome analysis counts. The study’s short treatment period and group sizes limit how much can be inferred about uncommon events or longer-term safety. The registry record does not provide enough information in these summaries to assess comparative risk precisely.

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

The posted primary results show that mean composite-score changes were similar in broad scale across the treatment groups and placebo, with recalculated between-group differences close to zero relative to their uncertainty. The sponsor’s ANCOVA effect sizes are also modest in point estimate, and all reported intervals include zero. These findings describe the data collected in this trial; they do not prove that the treatments are equivalent, and they do not establish that an armodafinil dosage produces a cognitive benefit.

Uncertainty is central to interpretation. The confidence intervals allow effects in either direction, and their breadth means that the trial does not precisely determine the magnitude of any difference. A lack of a statistically clear difference is not proof that no effect exists. Conversely, an estimate in a direction that might favor a treatment does not establish a reliable or important effect when uncertainty remains broad. The registry does not report a threshold for a clinically meaningful change, so the clinical importance of the numerical estimates cannot be determined from these summaries alone.

The outcome is a cognitive composite over a 4-week period or to the last post-baseline observation. It does not establish the effect on every cognitive domain, longer-term outcomes, or outcomes not assessed in the record. The secondary results add context but involve many measures, and multiplicity procedures are not reported. Their pattern should not be treated as a substitute for a clear primary result.

The study’s completed status and randomized, double-blind, placebo-controlled design are relevant features, but design labels do not remove limitations from small analysis groups, missing-data uncertainty, or incomplete reporting of the statistical plan. These findings should be understood as trial evidence with limited precision, not as individualized medical guidance. The registry results alone do not determine whether a treatment is appropriate for any person.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should be interpreted through the difference between groups, not by looking only at whether each group’s mean improved from baseline. The placebo group also had a positive mean change in the primary composite. Within-group change can reflect many influences, so it cannot isolate the contribution of the assigned treatment. The randomized placebo comparison is the relevant design feature for assessing a treatment contrast.

It also shows the importance of distinguishing an estimate from its precision. The point estimates for the primary comparisons are near zero on the score-unit scale, but the intervals are broad and include values in both directions. A small point estimate is not, on its own, evidence that a meaningful effect has been excluded. The same caution applies to a non-significant p-value: it is not a test of equivalence, and it does not describe the probability that a treatment works.

The record makes a useful contrast between a sponsor-reported adjusted analysis and simple unadjusted recalculations. Their estimands and scales differ, so they should not be collapsed into a single number. Examining both can help readers understand how the posted group means relate to the reported model-based effects, while keeping the sponsor’s analysis distinct from supplementary summaries.

Finally, multiple cognitive outcomes and a short endpoint timeframe make multiplicity and missing-data reporting important. A broad set of measures may be useful for characterizing cognition, but it also creates more opportunities for chance findings. Without a reported hierarchy or adjustment strategy, secondary findings deserve less weight than a well-interpreted primary comparison. The study is therefore a useful example of how design, endpoint definition, uncertainty, and reporting completeness shape the conclusions that can responsibly be drawn.

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 outcome analysis is based on a defined analysis population requiring at least one post-baseline efficacy assessment, rather than an explicitly described all-randomized-participant analysis. The record reports observed-data summaries and a rule for missing composite components, but it does not provide the extent or pattern of missing outcome data by group, detailed missing-data assumptions, or sensitivity analyses. This makes it difficult to assess how missing observations may have influenced the posted estimates.

The registry does not report the original sample-size rationale, intended randomization ratio, detailed randomization procedures, or complete statistical analysis plan. The ANCOVA model’s full covariate specification is also not reported. These omissions limit assessment of whether the posted analysis fully reflects the planned primary analysis. The registry does not report an outcome hierarchy or multiplicity strategy despite multiple secondary outcomes and analyses.

The trial evaluated a 4-week treatment period, and the primary outcome allowed the last observation after baseline rather than requiring a Week 4 observation for every participant. The primary groups contributing to the summaries were small, and the confidence intervals are broad. The record does not state a threshold for a clinically meaningful difference, which limits interpretation of whether any estimated change would matter in practice.

The secondary outcomes cover cognitive domains, but results across many outcomes can be difficult to interpret without prespecified priorities and multiplicity handling. The posted safety summaries provide counts, but they do not supply detailed event timing, attribution, or group-specific breakdown for the listed psychotic disorder term. Death counts are not reported in the registry record. These limitations leave important questions about precision, missingness, outcome selection, and safety detail unresolved.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Armodafinil as Adjunctive Therapy in Schizophrenic Adults With Cognitive Deficits — NCT00487942.
• Registry record last updated 2013-07-19; status last verified 2013-07.
• Results first posted 2010-12-20.
• 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

NCT00487942 is a completed randomized, double-blind, parallel-group, placebo-controlled Phase 2 study of adjunctive armodafinil in adults with cognitive deficits associated with schizophrenia. The registry lists 60 enrolled participants and a 4-week fixed-dosage treatment period comparing 50 mg/day, 100 mg/day, and 200 mg/day with placebo. The primary outcome was mean change in MATRICS Consensus Cognitive Battery composite score to the last observation after baseline.

The reported ANCOVA effect sizes were -0.04, 0.09, and 0.15 for the three armodafinil dosages versus placebo; all corresponding 95% confidence intervals included zero. Simple unadjusted recalculations likewise had broad intervals including zero. The registry lists multiple secondary cognitive outcomes, but multiplicity procedures and detailed missing-data methods are not reported. The posted results are therefore uncertain and should be interpreted as estimates from a short, small-group trial, not as proof of equivalence or a definitive treatment effect.