Cannabidiol in Youth Alcohol Use Disorder: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cannabidiol in Youth Alcohol Use Disorder (NCT05317546), a randomized phase 2 study. The primary outcome is Concentrations of Glx (i.e., Glutamate + Glutamine).

2. Clinical Question

3. Trial Design

This is a completed randomized phase 2 study sponsored by the Medical University of South Carolina. The registry lists a crossover model and random allocation. Its summary describes a within-subjects crossover design in which youth receive CBD or placebo in counterbalanced order. In a crossover study, each participant can contribute measurements under both conditions, so the comparison is within the same individuals rather than between two wholly separate groups.

The summary describes 600 mg of CBD or placebo administered three hours before a neuroimaging and behavioral assessment paradigm, with participation expected to last approximately one month. The registry lists quadruple masking, while the summary calls the study double-blind. The record does not explain the difference in these descriptions. It lists 36 enrolled participants. The summary had described a plan for 50 youth; the reason the completed enrollment differs from that planned number is not reported in the registry record.

The study began on 2022-10-01, reached primary completion on 2024-06-25, and is marked completed. For the primary outcome, the posted condition-level counts are 34 for CBD and 35 for placebo. These are outcome counts for the conditions, not a statement that the trial enrolled separate groups of that size. Why the outcome counts are not the same is not reported in the registry record.

The posted primary outcome is continuous: absolute Glx concentration in mmol/kg, measured in the anterior cingulate cortex. The registry lists five outcome measures and five analyses, but does not report a detailed analysis plan, the crossover sequence analysis, or a sample-size justification. It also does not report whether period or sequence effects were assessed.

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: All participants that were eligible and enrolled in the study (N= 36) completed randomized to a group.

First Allocation

First Wash-Out Period

Reasons for not completing this period:

Second Allocation

Second Wash-out Period

5. Baseline Characteristics

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

Population: All participants who were eligible and enrolled completed randomization.

6. Primary Endpoint

The registry lists the primary outcome as Concentrations of Glx (i.e., Glutamate + Glutamine), measured over Changes 3 hours after administration of 600mg CBD vs. placebo.

The primary endpoint is the concentration of Glx, defined as glutamate plus glutamine, in the anterior cingulate cortex. It is measured using magnetic resonance spectroscopy and reported as an absolute value in mmol/kg. The registry describes measurements taken three hours after administration of 600mg CBD or placebo. The endpoint is continuous, and the posted condition summaries are means with standard deviations.

As a general statistical matter, a continuous biological measurement can help characterize whether the observed values differ between study conditions and how variable those values are. Here, the registry identifies Glx as a neurochemical measure relevant to the study’s neurobehavioral assessment. It does not report that the measure is a validated clinical outcome or that a particular value corresponds to improvement or harm.

The registry explicitly notes that normal Glx levels are not known for this purpose. It therefore cautions against interpreting a higher or lower concentration as inherently better or worse. The endpoint can describe the measured biochemical response under the study conditions, but it cannot by itself establish a clinical benefit, a meaningful threshold, or the broader effect of CBD on alcohol use disorder.

7. Results Posted in the Registry

• Cannabidiol (600mg): mean 18.76 versus 18.57 on control; difference 0.19 (95% CI -0.31 to 0.69), standardized effect d = 0.18; z-test p = 0.460.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a continuous measurement, so the posted summaries use means and standard deviations. A mean describes the average value in a condition; a standard deviation describes how spread out individual measurements are around that average. These summaries are useful for describing the observed concentrations, but they do not by themselves account for the paired structure expected when participants are measured under both conditions.

The registry reports a sponsor analysis using mixed models and gives p = 0.33 for the superiority analysis. In general, mixed models can represent related observations and account for dependencies in the data, such as repeated measurements from the same participant. The specific model terms, covariance structure, handling of period or sequence, and estimation details are not reported in the registry record. Those details matter for understanding precisely how the crossover information was used.

A second, unadjusted comparison was recalculated from the posted summary statistics. It estimates the mean difference as 0.19 mmol/kg, with an interval spanning negative and positive values and an unadjusted p-value of 0.46. This is a simple comparison of the posted summaries, not the sponsor’s mixed-model analysis. Because the record does not report the within-participant covariance or the paired participant-level data, the recalculation cannot reproduce the full information potentially available from a crossover analysis. It should be interpreted as a supplementary description, not as an independently fitted crossover model.

As a general concept, an interval around an estimate represents a range of values compatible with the data under the method used and its assumptions. An interval that crosses zero for a mean difference is compatible with effects in either direction, as well as with little or no difference. It does not prove that the true difference is zero. The confidence level and detailed construction of the sponsor’s interval are not reported; the recalculated interval is also not assigned a confidence percentage in the registry record.

As a general matter, crossover studies can improve efficiency because each participant can serve as their own comparator, reducing the influence of stable differences between participants. That advantage depends on valid measurements in both conditions and appropriate treatment of within-person dependence. It also requires attention to the order and timing of conditions. The summary states that order was counterbalanced, but whether the analysis adjusted for period, sequence, or other crossover features is not reported in the registry record.

Variation matters when interpreting a mean difference. Greater variability generally makes an estimate less precise for a given amount of information, while repeated measurements may improve precision when within-person values are sufficiently correlated. The condition standard deviations are 0.98 mmol/kg after CBD and 1.15 mmol/kg after placebo. The paired correlation and individual-level differences are not reported, so the contribution of within-person pairing to uncertainty cannot be assessed from the registry summaries.

The registry also reports a planning illustration based on the observed effect. Such calculations ask how many participants per arm would be needed under specified assumptions to detect a chosen fraction of that effect at a selected power. They are hypothetical planning calculations, not evidence about what the completed trial was capable of detecting. The original sample-size assumptions and justification for the trial’s planned enrollment are not reported in the registry record.

Multiplicity refers to the statistical consequences of examining multiple outcomes, comparisons, or analyses. The registry lists five outcome measures and five analyses, but identifies no secondary outcomes as posted. It does not report whether a multiplicity adjustment was planned or used, or which analysis was designated as primary in a complete statistical analysis plan. The record therefore does not support a detailed assessment of how the reported p-value fits into a broader family of tests.

Missing-data methods and analysis-population definitions are also important in a crossover study. The record reports condition-level outcome counts but does not report reasons for unavailable measurements, the amount or pattern of missing data, imputation methods, or whether participants were analyzed according to a specified intention-to-treat or per-protocol definition. These omissions limit evaluation of the relationship between enrollment and the analyzed outcome data.

10. Confidence Intervals and Precision

The unadjusted mean difference is 0.19 mmol/kg. The posted recalculated interval extends from a negative value to a positive value, so it includes zero. This means the summary data are compatible with a range of possible differences in either direction under the recalculation’s assumptions. The record does not report the confidence level for this interval, so it should not be assigned a confidence percentage based on the registry information.

An interval is useful because it communicates uncertainty around an estimate rather than presenting the point estimate as exact. A narrow interval would indicate greater precision, while a wide interval would leave more uncertainty about the size and direction of the underlying difference. Here, the interval’s inclusion of both negative and positive values means the recalculated result does not sharply identify the direction of the difference. The interval does not establish equivalence and does not mean that all values within it are equally plausible.

The sponsor-reported mixed-model analysis gives p = 0.33, but the record does not include a model-based effect estimate or interval for that analysis. As a result, its precision cannot be judged directly from a sponsor-reported interval. The recalculated interval and the sponsor’s p-value come from different analytical approaches and should not be combined as if they were a single result.

Precision is also constrained by the posted outcome counts and the absence of participant-level paired information. The condition standard deviations describe the spread of measurements, but they do not reveal how closely each participant’s CBD and placebo measurements were related. The within-person correlation, analysis population, and handling of missing observations are not reported in the registry record. Those details would help readers understand the uncertainty in a crossover estimate.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are a planning illustration based on the observed effect, with two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the 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 hypothetical number of participants per arm under those assumptions for an 80% chance of detecting the selected effect if that effect were present. The 90% power column describes the corresponding planning target for a 90% chance. These are design calculations, not probabilities that the study’s finding is correct. The figures are not observed power.

For planning at 100% of the observed effect, the figures are 498 participants per arm for 80% power and 667 for 90% power. For planning at 75% of the observed effect, they are 885 participants per arm for 80% power and 1,185 for 90% power. For planning at 50% of the observed effect, they are 1,991 participants per arm for 80% power and 2,665 for 90% power.

Smaller effects require more participants under the same planning assumptions, because they are harder to distinguish from random variation. These illustrations use the observed effect as their starting point, so they should not be read as the original rationale for enrolling the trial’s planned 50 youth. The registry does not report the assumptions used for that original design.

12. 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 = 0.190; pooled standard deviation σ = 1.070.
2. n = 2 × (1.96 + 0.842)² × 1.070² / 0.190² = 497.5, rounded up to 498 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 <- 0.190000000000001                      # observed difference in means
sigma <- 1.06965052180886                     # 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(5317546)
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 = 498 (80% power), 667 (90% power)
 75% of observed effect: n per arm = 885 (80% power), 1,185 (90% power)
 50% of observed effect: n per arm = 1,991 (80% power), 2,665 (90% power)
power.t.test: 498.5 
Simulated power at n = 498 per arm: 0.795 (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.

13. Analyses Reported by the Sponsor

The sponsor-reported result is a mixed-model superiority analysis with p = 0.33. The unadjusted recalculation from the posted condition summaries estimates a mean difference of 0.19 mmol/kg, gives an interval spanning zero, and has p = 0.46. The sponsor result is the trial’s own reported analysis; the recalculation is a simpler supplementary analysis, not a second sponsor model.

Different analysis methods can yield different estimates of uncertainty and p-values, particularly when a design includes repeated measurements. The registry does not report enough model detail or participant-level data to determine why these two p-values differ or to reproduce the mixed model. No discrepancy between the posted result and recalculation is flagged in the registry record. The two results should therefore be kept distinct rather than averaged or treated as interchangeable.

The sponsor result does not include a model-based effect estimate or confidence interval in the registry record. That limits comparison of the magnitude and precision of the mixed-model result with the unadjusted estimate. The recalculation alone should not be used to infer that the sponsor’s analysis found a particular effect size.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists five outcome measures and five analyses, while the primary outcome is the Glx concentration in the anterior cingulate cortex. It reports no secondary outcomes as posted. These counts indicate that several measures or analyses were registered, but do not establish that all were tested as confirmatory hypotheses or that all results are available in the registry record.

Multiplicity arises when several statistical tests are considered together. As a general statistical matter, the more tests that are conducted, the greater the chance that at least one result may appear notable by chance if each test is interpreted separately. Methods such as prespecifying a primary outcome or adjusting a decision threshold can address this issue, but whether any such approach was used is not reported in the registry record.

The record does not provide a full statistical analysis plan, a hierarchy of outcomes, a multiplicity adjustment, or the rationale for which analyses were considered primary. It also does not report interim analyses. These details should not be assumed from the presence of a primary outcome designation or the listed analysis count.

Missing-data handling and analysis populations are similarly unclear. The condition-level outcome counts are 34 for CBD and 35 for placebo, compared with total enrollment of 36. The record does not explain why the counts differ, whether observations were missing, how missingness was assessed, or how any unavailable measurements were handled. Definitions such as intention-to-treat, modified intention-to-treat, and per-protocol populations are not reported in the registry record. Without these details, readers cannot determine precisely which participants contributed to the mixed-model result or how robust it is to missing observations.

For the crossover design, the record also does not report whether all participants completed both conditions or how incomplete pairs were treated. The within-participant correlation and analysis of period or sequence are not reported. These omissions prevent a full assessment of how the design’s paired structure, multiplicity, and missingness were handled.

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

The registry reports no serious adverse events in either condition: zero affected participants among 34 at risk after CBD and zero among 35 at risk after placebo. It also reports zero deaths in both conditions. These counts describe the posted serious-event data for the listed at-risk groups.

For other adverse events, the record reports two affected participants among 34 at risk after CBD and two among 35 at risk after placebo. These are counts, not a detailed account of event type, timing, severity, or relationship to the study condition. The registry lists no top serious-event terms.

As a general statistical matter, a count of zero observed serious events does not establish that an event cannot occur, and small event counts provide limited information about uncommon outcomes. The registry record does not provide further detail about safety surveillance or how adverse events were attributed to each condition. These figures should be read as the reported counts, not as a conclusion about safety in other populations or settings.

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

The posted results describe mean Glx concentrations after CBD and placebo and report a sponsor mixed-model p-value of 0.33. The unadjusted recalculation estimates a mean difference of 0.19 mmol/kg, with an interval that includes zero and an unadjusted p-value of 0.46. Together, these results do not establish a clear difference in the measured concentration under the trial conditions.

That interpretation is not the same as showing that the conditions are equivalent. The registry does not report an equivalence margin, a non-inferiority design, or a corresponding analysis. A result that does not establish a difference can reflect uncertainty as well as a small underlying effect. The reported interval’s span across both directions reinforces that uncertainty in the unadjusted estimate.

The outcome is a biochemical measurement, not a direct measure of alcohol use, functioning, or a clinical endpoint. The record explicitly says that normal Glx levels are not known and that the meaning of higher or lower concentrations cannot be determined from this comparison. Therefore, the observed direction of the mean difference cannot be interpreted as beneficial or harmful on the basis of the registry results.

The findings apply to the registered study conditions: a 600 mg dose, an assessment three hours after administration, and youth with alcohol use disorder in a crossover study. The record does not establish what would happen with other doses, longer-term use, other populations, or different outcomes. The result also cannot establish an effect on alcohol use disorder itself.

The study was completed with 36 enrolled participants, and the primary outcome condition counts were 34 and 35. The registry does not explain the difference between enrollment and those outcome counts or fully describe how the outcome analysis was conducted. These limitations, along with the absence of a sponsor-reported effect interval, constrain conclusions about the magnitude and precision of the model-based result.

17. Why This Trial Matters Statistically

This trial illustrates why the analysis should reflect the study design. A crossover trial measures participants under more than one condition, so the data can contain within-person information that is not represented by condition means alone. The registry’s sponsor analysis uses mixed models, while the supplementary recalculation uses posted summary statistics. Keeping those methods distinct prevents a simple unadjusted result from being mistaken for the full crossover analysis.

It also shows why an estimate and its uncertainty matter alongside a p-value. The mean difference is 0.19 mmol/kg, but the unadjusted interval includes values on either side of zero. A single p-value cannot convey the full range of effects compatible with the data, and it cannot indicate clinical importance. The registry’s caution about unknown normal Glx levels further separates statistical comparison from clinical interpretation.

The planning illustration offers another useful statistical lesson: sample-size requirements depend on the effect size targeted and the desired power. Smaller target effects require more participants under the stated planning assumptions. These figures are not the design rationale for the completed study, and the original rationale is not reported in the registry record.

Finally, the record demonstrates the importance of transparent analysis details. The mixed-model specifications, handling of missing measurements, analysis populations, multiplicity approach, and crossover period or sequence handling are not reported. Without these details, readers can identify the main result and its limits, but cannot fully reconstruct the statistical analysis or assess all of its assumptions.

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.

The primary outcome is an absolute Glx concentration, but the registry states that normal levels are not known and that the meaning of a higher or lower value cannot be determined. This limits clinical interpretation even if the statistical difference were estimated precisely. The outcome is also a biochemical measure rather than a direct measure of alcohol use or a clinical response.

The trial enrolled 36 participants, while the registry summary had described a plan for 50 youth. The reason for this difference is not reported in the registry record. The primary outcome counts are 34 for CBD and 35 for placebo, and the record does not explain the difference between those counts and total enrollment or whether any observations were missing.

The trial uses a crossover design, but the participant-level paired data and within-person correlation are not reported. The registry does not give full mixed-model specifications, or state whether period and sequence were included. This prevents an independent reconstruction of the sponsor analysis from the posted means and standard deviations.

The sponsor-reported mixed-model result has no posted effect estimate or interval. The supplementary unadjusted calculation provides an estimate and interval, but it does not replace the sponsor analysis. A complete statistical analysis plan, analysis-population definitions, missing-data methods, multiplicity procedures, interim analyses, and original sample-size assumptions are not reported in the registry record.

The registry lists five outcome measures and five analyses but no secondary outcomes as posted. This limits assessment of the full outcome and analysis landscape. The trial is also specific to the stated dose and three-hour assessment timing; the registry does not support generalization to other doses, durations, populations, or endpoints.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Cannabidiol in Youth Alcohol Use Disorder — NCT05317546.
• Registry record last updated 2025-08-14; status last verified 2025-07.
• Results first posted 2025-08-14.
• 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.

22. Record Summary

NCT05317546 is a completed randomized phase 2 crossover trial sponsored by the Medical University of South Carolina. It enrolled 36 participants and studied cannabidiol in youth with alcohol use disorder. The summary describes 600 mg CBD or placebo administered before a neuroimaging and behavioral assessment, with counterbalanced condition order.

The primary outcome was absolute Glx concentration in the anterior cingulate cortex, measured by magnetic resonance spectroscopy three hours after administration. The posted means were 18.76 mmol/kg after CBD and 18.57 mmol/kg after placebo. The sponsor-reported mixed-model superiority analysis gives p = 0.33; the unadjusted recalculation gives p = 0.46.

The registry cautions that normal Glx levels are unknown, so the direction of the measured difference does not establish clinical meaning. The record does not report full model specifications, missing-data methods, analysis populations, or original sample-size assumptions.