Tolcapone in Obsessive Compulsive Disorder: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Tolcapone in Obsessive Compulsive Disorder (NCT03348930), a randomized phase 2, phase 3 study. The primary outcome is Yale Brown Obsessive Compulsive Scale (Y-BOCS).

2. Clinical Question

The clinical question is therefore about a short-term difference in a symptom severity scale under two treatment conditions in a small crossover pilot. The record supports describing the estimates and their uncertainty, but does not report a detailed analysis of the crossover structure or a threshold for a clinically important score difference.

3. Trial Design

The registry identifies a randomized, quadruple-masked, crossover study of tolcapone and placebo for obsessive-compulsive disorder. Its official title calls the study double-blind, while the masking field says quadruple. The brief summary describes random assignment to the first treatment phase on a 1:1 basis, followed by a washout and then the alternate condition. The registry lists planned enrollment of 20 and marks the study completed.

Several record descriptions do not align precisely. The brief summary describes a five-week study with two-week treatment periods and a one-week washout. The arm descriptions refer to a four-week tolcapone treatment phase and a four-week placebo phase, while the primary endpoint timeframe describes assessment over two-week periods. The registry’s general study description identifies a two-week active period and a two-week placebo period. These variations make the intended timing less clear than the broad crossover sequence.

A crossover design allows a participant to receive both study conditions, which can make within-participant comparisons informative. General statistical considerations include whether the effects of treatment persist into the next period, whether outcomes change over time independently of treatment, and whether treatment sequence is accounted for. The registry record does not report how period, sequence, or carryover effects were handled, or whether the posted comparison used a paired analysis.

The sponsor was the University of Chicago. The primary analysis population was defined by receipt of at least one dose of each intervention and completion of all study visits. Although the registry gives that definition, it does not describe how missing measurements were handled or report the number excluded under each part of the definition. It lists no reported analyses for the primary outcome and no reported analyses for the detailed secondary outcomes.

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.

First Intervention (2 Weeks)

Washout (1 Week)

Reasons for not completing this period:

Second Intervention (2 Weeks)

Analysis population for the primary outcome, as defined in the registry: All participants who received at least one dose of each intervention and completed all study visits were included in the efficacy analysis.

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 Yale Brown Obsessive Compulsive Scale (Y-BOCS), measured over 2 weeks (start of study to washout period OR two weeks following washout period).

The primary endpoint was mean change in Y-BOCS score. The Y-BOCS assesses the severity of obsessive-compulsive disorder symptoms and ranges from 0 to 40, with 0 representing no symptoms and 40 representing severe symptoms. A change score expresses how a participant’s recorded score differs from the reference assessment over the specified period.

The registry describes assessments every two weeks and after the one-week washout. It says change from baseline to after five weeks would be assessed, but the endpoint timeframe instead describes two-week intervals: from study start to washout or the two weeks following washout. This leaves the exact score contrast behind the posted summary unclear. The record does not give a separate clinically important difference threshold, so the size of a mean score contrast cannot by itself establish whether participants would regard it as important.

Using a continuous scale preserves information about the range of recorded scores rather than reducing outcomes to a binary category. A mean summarizes the average change in the analyzed participants, while the standard deviation describes variation in scores within each treatment condition. Those summaries help describe the data, but they do not show how the crossover sequence or repeated measurements were incorporated into the comparison.

7. Results Posted in the Registry

• Tolcapone: mean -4.24 versus -1.10 on control; difference -3.14 (95% CI -6.64 to 0.36), standardized effect d = -0.57; z-test p = 0.079.

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.

Clinical Global Impression- Severity and Improvement (CGI)

• 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:
  • Tolcapone: mean 3.78 versus 3.50 on control; difference 0.28 (95% CI -0.51 to 1.07), standardized effect d = 0.24; z-test p = 0.488.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tolcapone and the control. The interval gives the range of effects that remain compatible with the data.

Sheehan Disability Scale (SDS)

• 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:
  • Tolcapone: mean -2.68 versus -1.97 on control; difference -0.71 (95% CI -4.38 to 2.96), standardized effect d = -0.13; z-test p = 0.705.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tolcapone and the control. The interval gives the range of effects that remain compatible with the data.

Hamilton Anxiety Rating Scale (HAM-A)

• 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:
  • Tolcapone: mean -1.90 versus -1.60 on control; difference -0.30 (95% CI -2.99 to 2.39), standardized effect d = -0.07; z-test p = 0.827.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tolcapone and the control. The interval gives the range of effects that remain compatible with the data.

The registry names four secondary measures: Clinical Global Impression severity and improvement, Sheehan Disability Scale, Hamilton Anxiety Rating Scale, and Hamilton Depression Rating Scale. Detailed posted summaries are available for the first three; a detailed HAM-D result is not reported in the registry record. The posted secondary comparisons are all mean-based estimates, and their intervals include zero. Taken as a group, they do not provide a clearly precise pattern that would materially settle the primary question.

The secondary measures address related but distinct aspects of clinical status: global impression, disability, anxiety, and depression. That breadth can add context to a symptom-scale result, but different measures may capture different constructs and may respond differently over the study periods. Agreement or disagreement among them should not be treated as a simple vote for or against the primary result.

The secondary comparisons are unadjusted. When several outcomes are examined, the chance of finding an apparently notable result by chance can increase. General statistical practice may address this through a prespecified hierarchy or multiplicity adjustment, but neither approach is described in the registry record. Because the detailed secondary results are not listed as reported analyses and no multiplicity plan is reported, they carry less inferential weight than a primary outcome assessed under a prespecified analysis plan.

These outcomes are best viewed as exploratory context. They cannot compensate for uncertainty about the primary endpoint timing, the crossover analysis, or missing-data handling. The absence of a detailed HAM-D summary also means the registry does not support a complete numerical account of every named secondary measure.

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

• Clinical Global Impression- Severity and Improvement (CGI)
• Sheehan Disability Scale (SDS)
• Hamilton Anxiety Rating Scale (HAM-A)
• Hamilton Depression Rating Scale (HAM-D)

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods help translate observed scores into an estimate of a treatment contrast and a description of its uncertainty. The registry posts means, standard deviations, a mean difference, a confidence interval, and an unadjusted p-value for the primary outcome. It does not report a formal analysis description, and its reported analyses field is empty. The methods below explain how these statistics are generally read; they do not establish which full analysis procedure the study team used.

What does a mean change describe?

A mean change is the average of participant-level changes in the analyzed group. A negative value on the Y-BOCS means the recorded scores were lower at the later assessment than at the reference assessment on average. The mean condenses the group’s scores to one summary, so it does not show whether most participants had similar changes or whether the average reflects a range of individual outcomes. The standard deviation describes how dispersed the observed changes were around the mean; it is not the uncertainty interval for the mean itself.

The primary outcome is continuous, so mean-based summaries are a natural way to describe its distribution when those summaries are appropriate. General statistical practice also considers the shape of the data and the analysis design. The registry does not report diagnostic checks or explain whether the assumptions behind the comparison were assessed.

What does the mean difference represent?

The mean difference compares the posted mean change for tolcapone with the posted mean change for placebo. A negative contrast indicates a more negative mean change in the tolcapone condition under the subtraction convention used in the comparison. The estimate is a summary of the observed contrast, not a statement about every participant. It does not by itself distinguish treatment effects from period effects, carryover, or other features of a crossover study.

In a crossover trial, each participant may contribute outcomes under both conditions. General methods can use that pairing to account for the fact that measurements from the same person are related. A model may also account for treatment sequence and period. The registry does not say whether such features were included. The posted summary values and confidence interval therefore should not be assumed to represent a particular paired or period-adjusted model.

How should the confidence interval be read?

A confidence interval expresses uncertainty around an estimated contrast under the assumptions of the calculation. A narrower interval indicates greater precision; a wider interval indicates less precision. For the primary comparison, the interval ranges from -6.641 to 0.361 and includes zero. This means the data and calculation do not isolate a contrast on one side of zero. The interval is not a range containing every participant’s response, nor does it give the probability that the true effect lies within its endpoints.

The confidence level for the posted interval is not reported in the registry record. It is therefore appropriate to quote its bounds without assigning a confidence percentage. The interval also inherits limitations of the analysis that generated it; it cannot correct for an unreported crossover model or missing-data procedure.

What does the p-value add?

A p-value describes how unusual data at least as inconsistent with a specified no-difference assumption would be, if that assumption and the statistical model were correct. The primary unadjusted p-value is 0.079. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. It should be considered alongside the estimated mean difference, its interval, the design, and the completeness of the analysis record.

“Unadjusted” indicates that the reported p-value is not presented as adjusted for testing multiple outcomes. The registry does not state whether an adjustment was planned or how the primary and secondary outcomes were ordered in the analysis plan. The p-value cannot resolve those omissions.

Why does over-dispersion matter?

General statistical explanation: over-dispersion occurs when outcome variation is greater than a model assumes. If a model underestimates variability, standard errors can be too small and intervals too narrow; if it handles variability poorly, inferential summaries may be misleading. This concern is most directly relevant when the analysis relies on a distributional model. The registry reports standard deviations for the continuous outcomes but does not describe a model or report an assessment of over-dispersion. There is no basis in the record to say that over-dispersion occurred in this trial.

More broadly, the posted estimates are summaries, while the registry does not list reported analyses for the primary outcome. This limits the ability to assess the exact model, its assumptions, and whether the comparison follows the randomized crossover structure. The reported numbers remain useful as descriptive results, but a fuller statistical account would be needed to judge the analysis in detail.

11. Confidence Intervals and Precision

Precision concerns how tightly the data locate an estimated contrast. The primary mean difference is -3.14, and its confidence interval runs from -6.641 to 0.361. The interval spans values on both sides of zero, so the posted result does not precisely distinguish a negative contrast from no difference or a small contrast in the opposite direction. Its width is important: the point estimate alone gives a much more definite impression than the range of values compatible with the calculation.

The interval does not represent the spread of individual score changes. The standard deviations for the tolcapone and placebo mean changes are 6.2 and 4.71, respectively; those describe participant-level variability in the treatment summaries, not the uncertainty in the difference. The number of participants in each primary summary is 19. With a pilot of this size, individual observations can have appreciable influence on group summaries, although the registry does not report influence diagnostics.

The confidence level and exact inferential procedure for the interval are not reported. The crossover design raises an additional precision question: a paired analysis can use within-participant information, while an analysis that does not account for pairing may not represent the intended design. The registry does not say which approach produced the posted interval. Thus, the bounds convey the uncertainty of the posted comparison, but do not establish that all design-related uncertainty has been addressed.

Precision and clinical importance are distinct. The registry does not state a threshold for a meaningful Y-BOCS change, so the interval cannot be classified as clinically important or unimportant using a trial-specific benchmark. It shows that the estimate is uncertain, not what participants would value.

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. The registry does not report the original sample-size justification. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the target effect is the stated fraction of the observed effect. These are illustrative calculations, not a reconstruction of the study’s protocol.

The figures are participants per arm for 80% power and participants per arm for 90% power. In plain terms, the 80% column gives the illustrative number in each arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and assumptions were correct. The 90% column uses a higher target chance of detection and therefore calls for more participants per arm. These are planning quantities, not observed trial outcomes.

Rows planning for 100%, 75%, or 50% of the observed effect represent progressively smaller effects to detect. Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions. The resulting figures can become large when the effect used for planning is small. They should not be read as recommended enrollment targets without considering the study design and the uncertainty in the pilot estimate.

These calculations use a two-arm framework with equal allocation, while the trial itself is described as a crossover study. A crossover design has different dependence between treatment observations than a conventional parallel-arm design. The registry’s planning illustration does not state that it models this crossover structure. The figures are not observed power, and they do not indicate the probability that the trial’s result is correct.

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 = -3.140; pooled standard deviation σ = 5.506.
2. n = 2 × (1.96 + 0.842)² × 5.506² / -3.140² = 48.3, rounded up to 49 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 <- -3.14                      # observed difference in means
sigma <- 5.50563801933981                     # 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(3348930)
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 = 49 (80% power), 65 (90% power)
 75% of observed effect: n per arm = 86 (80% power), 115 (90% power)
 50% of observed effect: n per arm = 194 (80% power), 259 (90% power)
power.t.test: 49.2 
Simulated power at n = 49 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. Multiplicity, Missing Data and Analysis Populations

The registry names a primary outcome and several secondary outcomes, but does not report a statistical analysis plan or a multiplicity strategy. It does not say whether the outcomes were tested in a prespecified order, whether any adjustment was planned, or which findings were intended to be confirmatory. The posted secondary comparisons are unadjusted, so they should be treated cautiously when considered alongside one another. The record lists no reported primary analyses and no reported analyses for the detailed secondary outcomes.

The primary efficacy population is defined as participants who received at least one dose of each intervention and completed all study visits. This is a complete-visit population definition, but the registry does not report how many participants failed to meet it or why. Nor does it describe whether missing measurements were excluded, imputed, or addressed through another method. The record therefore does not allow readers to assess whether missingness could have affected the estimates.

For a crossover trial, analysis choices also include treatment period, randomized sequence, and possible carryover from one period into the next. Those features can matter because measurements within a participant are related and the order of conditions may affect observed outcomes. The registry does not report whether these factors were modeled, tested, or otherwise handled. It also does not describe interim analyses or any protocol-based stopping rules.

These omissions limit evaluation of the inferential claims that can be attached to the posted values. They do not demonstrate that the study team failed to perform relevant analyses; they mean those methods are not reported in the registry record. The displayed estimates and intervals can still be described, but the analysis population, missing-data assumptions, multiplicity control, and crossover modeling cannot be independently assessed from the registry account.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

For serious adverse events, the record reports 20 participants at risk in each condition and zero affected participants in both the tolcapone and placebo groups. It reports zero deaths in each condition. No serious adverse event terms are listed. These figures describe what was posted for the recorded risk groups; they do not establish that serious events are impossible or that the risk is absent.

The number at risk for these safety summaries is 20 per condition, while the primary efficacy summaries include 19 participants per condition. The record does not explain the difference in populations. The serious-event figures should therefore be read separately from the primary efficacy analysis population.

Other adverse events are distinct from serious adverse events: the record reports 3 affected participants for tolcapone and 5 for placebo in the other-adverse-event counts. These counts do not provide event-level detail or establish a comparative safety conclusion. The registry record does not report serious event terms, and the posted counts alone do not characterize event severity, timing, or relatedness.

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

The posted primary result is a mean difference in Y-BOCS change of -3.14 for tolcapone compared with placebo. The interval from -6.641 to 0.361 includes zero, and the unadjusted p-value is 0.079. These statistics describe an uncertain estimate, not a definitive answer about whether the treatments differ. They do not show that every participant changed in the same way, and they do not quantify a trial-specific threshold for meaningful change.

The outcome is a symptom-severity scale, and the posted mean changes are negative in both conditions. The numerical pattern is consistent with lower average scores at the measured point than at the reference point in both treatment summaries. The comparison alone cannot establish why scores changed, nor whether the difference would matter to participants. The registry does not report a clinically important difference benchmark.

The results also need to be understood within the design. The trial was randomized and crossover, but the registry does not report whether the analysis accounted for participant pairing, sequence, period, or carryover. The outcome timing is described inconsistently, and missing-data handling and multiplicity methods are not reported. These features limit how confidently the displayed contrast can be interpreted as a treatment-specific effect.

The sample-size illustrations are planning exercises, not evidence about the probability that the trial detected an effect. The study’s planned enrollment was 20, and the primary summaries include 19 in each condition. The small pilot scale and the broad confidence interval make the estimate imprecise. Secondary outcomes provide additional exploratory context but are unadjusted and do not replace a fully reported primary analysis.

Accordingly, the record supports a careful description of observed means, their difference, and uncertainty. It does not justify a claim that tolcapone works or does not work, nor does it support a conclusion about clinical benefit or lack of benefit. A fuller interpretation would require clearer endpoint timing and reporting of the analysis methods and missing-data procedures.

17. Why This Trial Matters Statistically

This trial is statistically informative because it combines a randomized treatment sequence with a crossover design and a continuous symptom measure. A crossover can permit comparisons within the same participant, which may be useful when outcomes vary considerably between people. At the same time, it requires attention to the relationship between repeated measurements and to the order and timing of treatment conditions. The registry’s limited analysis detail makes that distinction especially important when reading the posted contrast.

The primary estimate illustrates why a point estimate should not be interpreted alone. The mean difference is -3.14, but its interval extends across zero. The estimate conveys the direction and size of the posted contrast, while the interval conveys that a wide range remains compatible with the calculation. This is a practical example of how precision affects the strength of a statistical interpretation, independent of whether a result appears notable at first glance.

The record also shows how registry descriptions shape interpretation. The study duration and endpoint timing vary across the summary, arm descriptions, and primary outcome timeframe. The masking description differs between the official title and the masking field. These differences do not change the posted numbers, but they complicate assessment of exactly which treatment-period comparison those numbers represent.

Finally, the record offers planning illustrations based on the observed effect while leaving the original design justification unreported. Distinguishing retrospective planning illustrations from the trial’s own design rationale prevents the calculations from being mistaken for evidence about the study’s actual power. The example underscores the value of reporting analysis plans, crossover methods, multiplicity decisions, and missing-data handling alongside outcome summaries.

18. Limitations

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

Several trial-specific limitations affect interpretation. The primary endpoint timing is not consistently described: the registry refers both to a five-week assessment and to two-week treatment-period comparisons around washout. The arm descriptions also refer to four-week phases, in contrast with the brief summary’s two-week phases. The record does not resolve which description corresponds to the posted outcome values.

The design is described as crossover, but the registry does not report whether the comparison accounts for pairing, period, randomized sequence, or carryover. No reported analyses are listed for the primary outcome. The confidence interval and unadjusted p-value are posted, but the exact analysis procedure and confidence level are not stated. This prevents a detailed assessment of whether the inferential summaries match the intended design.

The primary analysis population requires participants to receive at least one dose of each intervention and complete all visits. The registry does not report the number of participants excluded from this population or how missing outcomes were handled. The safety summaries use 20 participants at risk in each condition, whereas the primary efficacy summaries include 19 in each condition; the reason for that difference is not described.

The registry does not report a sample-size justification, multiplicity plan, clinically important difference, or detailed analysis plan. It lists four secondary measures, but detailed results are not posted for HAM-D. These reporting gaps do not establish that methods were not used; they limit what can be verified from the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Tolcapone in Obsessive Compulsive Disorder — NCT03348930.
• Registry record last updated 2022-04-07; status last verified 2022-03.
• Results first posted 2022-04-07.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT03348930 is a completed randomized crossover pilot study of tolcapone and placebo in people with obsessive-compulsive disorder. The registry lists planned enrollment of 20 and identifies Y-BOCS mean change as the primary outcome. The posted primary summaries include 19 participants in each condition and report a mean difference of -3.14, with an interval from -6.641 to 0.361 and an unadjusted p-value of 0.079.

The result is imprecise, and the registry does not report a crossover-specific analysis, missing-data procedure, multiplicity plan, or original sample-size justification. Descriptions of treatment duration and endpoint timing are inconsistent. The record also lists secondary outcomes and safety counts, but these do not resolve the limitations in interpreting the primary comparison.