Enhancing the Effects of Adolescent Alcohol Treatment With Atomoxetine: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Enhancing the Effects of Adolescent Alcohol Treatment With Atomoxetine (NCT04565288), a randomized phase 2 study. The primary outcome is Completion Rates.

2. Clinical Question

The registry describes two primary objectives. One concerned feasibility, acceptability, and tolerability of atomoxetine compared with placebo when both were paired with the psychosocial platform. The other concerned intermediate phenotypes associated with alcohol use and clinical-trial outcomes, assessed using a human laboratory paradigm and ecological momentary assessment methods.

The posted primary outcome is completion of the active medication phase, not a direct measure of alcohol consumption or a clinical measure of recovery. Completion can describe whether participants remained in the medication phase, but it does not by itself establish why participants completed or discontinued, how acceptable treatment was to them, or whether alcohol-related outcomes changed. The registry also lists alcohol craving as a secondary outcome, assessed after alcohol-cue exposure in a laboratory paradigm. The results therefore address several different aspects of the study question, and they should be interpreted according to the particular outcome each represents.

3. Trial Design

The registry describes a phase 2, randomized, parallel-group trial with quadruple masking. It lists atomoxetine and placebo as the two drug interventions and describes matching placebo capsules. The atomoxetine regimen was 40 mg/day for 3 days, then 80 mg/day thereafter, during a 6-week medication trial. Both groups received a psychosocial platform comprising motivational enhancement therapy and cognitive behavioral therapy.

The trial population was adolescents ages 14 to 19 years with alcohol use disorder confirmed by DSM-5. The registry lists enrollment of 42 and reports 21 participants in each group for the primary completion outcome. The study status is completed. The registry record gives a start date of 2021-05-06 and a primary completion date of 2023-05-16.

The primary outcome was completion of the 6-week active treatment phase, reported as a count of participants. The outcome description says that the number and percentage completing the medication phase would determine feasibility. Alcohol craving was listed as a secondary outcome, assessed at week 5 after exposure to alcohol and water cues in a laboratory paradigm. The registry record does not provide a more detailed account of the masking roles or procedures, nor does it report the original design assumptions for the trial's sample size.

The design places the medication comparison within a shared psychosocial treatment context. The posted group contrast therefore concerns assignment to atomoxetine versus placebo alongside that platform, rather than atomoxetine in isolation. Random allocation can help make groups comparable in expectation, but the posted outcome counts alone cannot establish that all other influences were balanced. The registry record does not report a separate analysis of the effects of the psychosocial platform.

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.

Overall Study

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 Completion Rates, measured over 6-week active treatment phase.

The primary endpoint counts participants who completed the active medication phase over the 6-week treatment period. The registry describes this count, together with the percentage completing, as a way to assess feasibility. Completion is a practical trial outcome: it records whether participants reached the end of the active phase, rather than measuring a biological response or change in alcohol use.

For atomoxetine, 17 of 21 participants completed the phase; for placebo, 18 of 21 completed. The posted comparison expresses the group difference as a risk difference of -0.048, with a confidence interval from -0.273 to 0.177. The negative estimate represents a lower observed completion proportion in the atomoxetine group than in the placebo group. The interval is broad and includes differences in either direction, so the point estimate alone gives an incomplete account of uncertainty.

Completion is useful for describing whether a treatment regimen can be carried through a trial, but it is not equivalent to acceptability or tolerability. A participant may complete for many reasons, and the completion count does not identify those reasons. The registry record does not report the reasons for non-completion or a separate primary endpoint definition for acceptability or tolerability. Accordingly, the posted completion outcome addresses one aspect of the stated feasibility objective, not every component of that objective.

7. Results Posted in the Registry

• Atomoxetine: 81.0% (17/21) versus 85.7% (18/21) on control; risk difference -4.8 percentage points (95% CI -27.3 to 17.7), risk ratio 0.94 (0.72–1.24); unadjusted two-proportion z-test p = 0.679.

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.

Alcohol Craving

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Atomoxetine: 45.5% (5/11) versus 88.9% (16/18) on control; risk difference -43.4 percentage points (95% CI -76.2 to -10.6), risk ratio 0.51 (0.26–1.00); unadjusted two-proportion z-test p = 0.011.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Atomoxetine than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists alcohol craving as a secondary outcome, assessed after alcohol-cue exposure during a laboratory paradigm at week 5. Its posted counts compare participants with the event in each group, and the unadjusted comparison differs in direction from the primary completion estimate. This outcome addresses a different question from completion: it concerns craving ratings after cue exposure, not whether participants completed the active medication phase.

The secondary outcome can provide context for the trial's broader objective of examining intermediate phenotypes associated with alcohol use. It does not replace the primary feasibility-related endpoint, and it does not resolve the uncertainty around the completion contrast. Each outcome has its own measurement setting, denominator, and interpretation. Differences in outcome availability can also affect how directly the results can be compared; reasons for the differing denominators are not reported in the registry record.

The registry record lists no reported analyses for the secondary outcome. The posted unadjusted result therefore has less interpretive support than a result accompanied by a documented analysis plan and reporting of the analysis population. In addition, secondary outcomes are commonly considered alongside other outcomes, creating multiple opportunities to observe a nominally unusual result. The registry record does not report a multiplicity adjustment or a prespecified strategy governing interpretation of secondary tests.

These considerations mean the secondary result should be treated as less conclusive than a primary result that was central to the trial's stated objective. It may motivate further investigation, but the registry data alone do not establish a general pattern across a broader set of secondary endpoints: only one secondary outcome is posted. Its finding should be considered alongside its uncertainty, the limited documentation of analysis procedures, and the primary result rather than taken as evidence that the overall trial objectives were met.

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

• Alcohol Craving

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a binary count outcome: participants who completed the active medication phase. For such an outcome, a group proportion is the count with the event divided by the number assessed in that group. The posted completion proportions are 0.809 for atomoxetine and 0.857 for placebo. These proportions describe the observed groups; they are not adjusted for other characteristics in the posted comparison.

What does the risk difference express?

A risk difference subtracts the event proportion in one group from the proportion in the comparison group. Here, the reported estimate is -0.048 for atomoxetine relative to placebo. The negative sign indicates that the observed completion proportion was lower in the atomoxetine group. A risk difference is expressed on the probability scale, so it describes an absolute contrast, not a relative change. The comparison's direction depends on which group is treated as the reference; the registry identifies placebo as the control.

How should the confidence interval be read?

A confidence interval describes the uncertainty around an estimated group contrast under the assumptions of the method used to construct it. The primary interval extends from -0.273 to 0.177. It includes zero, the value corresponding to no difference in completion proportions, as well as values on either side of zero. This breadth means that the observed estimate should not be treated as an exact measure of the underlying contrast. General statistical interpretation: intervals are more informative when read alongside the estimate and the outcome scale, rather than as a simple pass-or-fail test.

What does the p-value add?

The posted unadjusted p-value for completion is 0.679. A p-value describes how compatible the observed data are with a specified null model, under the analysis assumptions; it is not the probability that the null hypothesis is true. It also does not measure the probability that a result will replicate, nor does it show whether an effect is important. Because the posted result is unadjusted, the registry does not indicate that the p-value accounts for multiple outcome testing or covariates.

Why are relative measures also listed?

The registry also reports a risk ratio of 0.944, with an interval from 0.720 to 1.239, and an odds ratio of 0.708, with an interval from 0.138 to 3.641. A risk ratio compares event proportions as a ratio; an odds ratio compares event odds. These measures use different scales from the risk difference and can look numerically different while describing the same underlying group counts. Their intervals also span values consistent with more than one direction of contrast. The risk difference is especially direct for expressing an absolute change in the probability of completion, while relative measures can provide complementary descriptions.

These summary measures do not replace the underlying counts. Counts show how many participants had the event and the group denominators; the contrast estimates then express the difference in a chosen form. Intervals communicate uncertainty for those estimates. In a small study, estimates can be sensitive to a small number of outcomes, and the intervals can be wide. General statistical explanation: this is one reason to avoid treating a point estimate as a stable or definitive measure when the data contain limited information.

What does randomization contribute?

Random allocation is intended to reduce systematic differences between groups at assignment, including differences that are not measured. The registry labels the allocation randomized and the masking quadruple, but the record does not report the detailed allocation procedure, the identities of those masked, or whether masking was maintained throughout. Randomization supports the comparison's design, but does not eliminate uncertainty from the observed sample or resolve missing-data concerns.

What is not specified about the analysis?

The record reports counts and unadjusted comparisons, but it does not report a detailed statistical analysis plan, the analysis population, or covariate-adjustment procedures. It also does not report how missing outcome information was handled. The posted primary group denominators are 21 in each arm, but that alone does not establish the rules used to define the analysis population. Without those details, the summary statistics should be interpreted as the comparisons actually posted, not as evidence of an unreported model or analysis choice.

For the secondary craving result, the posted group denominators differ, and no analyses are listed in the registry's reported-analyses field. That contrast is therefore less fully documented than a result accompanied by a clearly described analysis plan and population. General statistical explanation: when outcomes are examined in addition to a primary endpoint, the number of opportunities to observe an apparently unusual result can increase. Interpretation should account for that context, especially when an unadjusted secondary p-value is available without a reported multiplicity procedure.

11. Confidence Intervals and Precision

The primary completion estimate is a risk difference of -0.048, with a 95% confidence interval from -0.273 to 0.177. The interval is wide relative to the point estimate and includes zero. It also includes values favoring either group. Consequently, the observed estimate does not specify the completion contrast precisely enough to support a narrow conclusion about its size or direction.

In general, a confidence interval is a range of estimates compatible with the observed data and the statistical procedure, under its assumptions. It is not a guarantee that the true value lies within the particular interval, and its endpoints are not a set of equally likely values. The interval is useful because it shows how much uncertainty accompanies the estimate, which a p-value alone cannot convey.

The risk ratio interval runs from 0.720 to 1.239, and the odds ratio interval runs from 0.138 to 3.641. Both span values on either side of their no-contrast reference value. These are alternative scales for expressing the same posted group comparison, not independent confirmations. The risk difference remains a direct way to judge absolute separation in completion proportions.

Precision is limited by the amount of information in the observed outcome counts and by the uncertainty inherent in sampling. The registry record does not report a prespecified precision target or the original assumptions used to plan the trial, so the precision should be assessed from the posted intervals rather than from a claim about what the study was designed to detect.

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 table and curve present planning illustrations based on the observed effect, not the trial's original design assumptions. For these binary outcomes, the figures are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is specified as a fraction of the observed effect.

The 80% power column gives the planned participants per arm for a hypothetical study with an 80% chance of detecting the chosen effect under those assumptions, if that effect and the statistical model were correct. The 90% power column describes a higher chance of detection and accordingly requires a larger planned sample for the same assumed effect. These are design calculations, not descriptions of what happened in the completed trial.

The rows representing 100%, 75%, and 50% of the observed effect illustrate how the planning result changes when the effect to detect is reduced. Smaller effects need more participants to distinguish them from random variation under otherwise unchanged assumptions. The required counts can therefore rise substantially as the target effect becomes smaller. This relationship is a general feature of sample-size planning, rather than evidence that a particular effect will occur in a future study.

For the primary completion result, the planning illustration uses the observed completion contrast; for the secondary result, it uses the observed craving contrast. Because observed effects from a small study can be unstable, using them as planning inputs can produce optimistic or otherwise uncertain projections. The registry record does not report the original sample-size justification or design assumptions. This is not observed power: the calculations are forward-looking planning illustrations, not a retrospective measure of the trial's ability to find an effect.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.857; treatment proportion p₁ = 0.810; average p̄ = 0.833.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5270 = 1.0330.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5260 = 0.4427.
4. n = (1.0330 + 0.4427)² / (-0.0476)² = 960.3, rounded up to 961 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
p0 <- 0.857142857142857                          # control proportion
p1 <- 0.80952380952381                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(4565288)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 961 (80% power), 1,286 (90% power)
 75% of observed effect: n per arm = 1,659 (80% power), 2,221 (90% power)
 50% of observed effect: n per arm = 3,622 (80% power), 4,848 (90% power)
power.prop.test: 960.3 
Simulated power at n = 961 per arm: 0.801 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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

Multiplicity arises when several outcomes or comparisons are examined. The more tests considered, the greater the opportunity for at least one result to appear unusual by chance, even when no corresponding underlying effect exists. The registry describes two primary objectives and lists alcohol craving as a secondary outcome, but it does not report a multiplicity plan, any adjustment method, or a hierarchy for interpreting tests. The posted p-values are unadjusted. They should not be read as if they necessarily account for all outcomes considered.

The registry record lists no reported analyses for the secondary outcome. It does not specify whether the secondary analysis was planned before the results were observed, whether additional outcomes were measured but not posted, or how the two stated primary objectives were handled analytically. These details are not reported in the registry record, so the posted comparisons cannot establish that multiplicity was controlled.

Missing-data handling is also not reported. For the primary completion outcome, the posted denominators are the same in both groups, but this does not state how participants with incomplete information would have been treated under the analysis rules. For the secondary outcome, the posted denominators differ between groups. The registry does not explain why, whether all randomized participants were eligible for that assessment, or whether missing outcomes were excluded or handled by another method.

The analysis populations are not reported in sufficient detail to determine whether comparisons followed an intention-to-treat approach, a per-protocol approach, or another definition. The record gives the randomized design and the posted outcome counts, but does not identify the population used for each analysis or describe any imputation. These omissions matter because analytic choices can influence estimates, especially when outcome availability differs between groups.

For transparent interpretation, a fuller report would describe prespecified outcomes, multiplicity handling, participant flow, analysis populations, and missing-data procedures. In their absence, the posted results remain useful as registry-reported summaries, but their inferential scope is limited to the comparisons and details actually recorded.

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 5% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures report zero affected participants in the atomoxetine group and zero in the placebo group, with 21 at risk in each group. The registry lists no serious adverse event terms. These entries describe what was reported for serious adverse events in the registry; they do not establish that no adverse experiences of any kind occurred.

The record also reports 19 participants affected by other adverse events in each group, with 21 at risk in each group. The registry does not provide the event terms in the serious-event listing, nor does the summary identify the nature, severity, timing, or relationship of the other adverse events to treatment. The figures are counts of participants affected, not a detailed account of each event.

Zero recorded serious adverse events in both groups should be read as an absence of reported events in these trial results, not as proof of no risk. The registry record does not provide enough detail to compare particular adverse-event types or to assess how events were collected and classified. These safety counts are descriptive and should be interpreted within the size and duration of the study, rather than generalized beyond the posted record.

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

The primary result describes completion of the 6-week active medication phase in a randomized comparison of atomoxetine and placebo, with both groups receiving motivational enhancement therapy and cognitive behavioral therapy. The observed completion counts were close, and the estimated risk difference was negative for atomoxetine relative to placebo. Its confidence interval spans zero and a range of contrasts in both directions. The posted data therefore do not establish a clear difference in completion between groups.

This is not evidence that the treatments are equivalent. Demonstrating equivalence or non-inferiority requires a design and analysis with prespecified margins, and those are not reported in the registry record. Nor does a non-significant unadjusted p-value prove that there is no difference. The interval indicates that uncertainty remains about the size and direction of the completion contrast.

The endpoint measures completing the medication phase, not alcohol use, remission, or long-term outcomes. It addresses one part of feasibility but does not, by itself, establish acceptability or tolerability. The secondary alcohol-craving outcome concerns a laboratory response after cue exposure and has different limitations, including a different posted denominator and no listed reported analysis. It should not be treated as confirmation or refutation of the primary result.

The results apply to the trial population and regimen described in the registry. They do not isolate medication effects from the shared psychosocial platform, and the registry does not report enough detail to assess how missing data, analysis populations, or multiple outcomes were handled. The safety entries report no serious adverse events in either group, but do not amount to proof that serious or other harms cannot occur.

In short, the registry results provide descriptive estimates with substantial uncertainty. They can inform statistical discussion of feasibility and further study planning, but they do not settle broader questions about treatment effects, long-term outcomes, or safety.

17. Why This Trial Matters Statistically

This trial is statistically informative because it distinguishes a practical feasibility endpoint from clinical outcomes that may be the focus of treatment research. Completion is measurable and relevant to whether a regimen can be carried through a study, but it is not a substitute for measuring alcohol use or other clinical outcomes. Keeping the endpoint's meaning clear prevents a completion comparison from being overinterpreted.

The primary estimate also illustrates why a point estimate should be read with its confidence interval. The observed risk difference is modest in the context of the reported scale, but its interval is broad and includes the no-difference value and contrasts in either direction. The data therefore show both the observed group pattern and the uncertainty that remains. A p-value alone would not communicate this range.

The registry also demonstrates how a secondary finding can attract attention despite limited analysis detail. The craving result is a different endpoint from completion, and its interpretation is less secure when the analysis population, missing-data handling, and multiplicity strategy are not reported. Statistical evidence is strongest when estimates are interpreted in the context of prespecification and transparent analytic methods, not solely by whether an unadjusted test crosses a conventional threshold.

Finally, the sample-size illustrations connect observed estimates to future planning, while also showing the sensitivity of planning to the effect chosen. They are not observed power and do not reveal the assumptions behind the original study design. This distinction matters: exploratory estimates can help frame future questions, but should not be mistaken for stable effects or definitive design inputs.

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 endpoint captures completion of the active medication phase but not the reasons for completion or discontinuation. It therefore cannot independently characterize acceptability or tolerability, despite those being part of the stated objectives. The registry record does not report reasons for non-completion or additional measures that would clarify those dimensions.

The primary risk-difference interval is broad, leaving meaningful uncertainty about the size and direction of the contrast. The trial's original sample-size assumptions and justification are not reported, so it is not possible to relate the observed precision to the study's intended design target. Planning illustrations based on the observed effect do not resolve that limitation.

The secondary craving outcome has different group denominators, and the registry record does not explain the difference. The reported-analyses field is empty, leaving the analytic population, model specification, and missing-data handling unreported. The record also does not describe a multiplicity plan despite the presence of multiple stated objectives and a secondary endpoint.

Although the study is described as randomized and quadruple masked, details of allocation procedures and which roles were masked are not reported. The registry does not provide a fuller account of participant flow, baseline characteristics, or the analysis population. These omissions limit assessment of potential imbalances and the robustness of the posted comparisons.

Finally, the primary outcome concerns a 6-week active treatment phase, while the registry does not report longer-term outcomes in these results. The posted counts and safety summary are descriptive and do not settle questions beyond the measured outcomes and period recorded.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Enhancing the Effects of Adolescent Alcohol Treatment With Atomoxetine — NCT04565288.
• Registry record last updated 2025-05-09; status last verified 2025-04.
• Results first posted 2025-05-09.
• 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

The registry describes NCT04565288, a completed phase 2 randomized, parallel-group trial with quadruple masking. It lists adolescents ages 14 to 19 years with alcohol use disorder and enrollment of 42. The intervention was atomoxetine, dosed at 40 mg/day for 3 days and 80 mg/day thereafter, alongside motivational enhancement therapy and cognitive behavioral therapy; the comparator was matching placebo with the same psychosocial platform.

The primary outcome was completion of the 6-week active medication phase. The posted counts were 17 of 21 in the atomoxetine group and 18 of 21 in the placebo group. The reported risk difference was -0.048, with a 95% confidence interval from -0.273 to 0.177 and an unadjusted p-value of 0.679. Alcohol craving after alcohol-cue exposure was listed as a secondary outcome. The registry record does not report a multiplicity plan, missing-data procedures, or detailed analysis populations.