Oxytocin, Alcohol Craving, and Intimate Partner Aggression: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Oxytocin, Alcohol Craving, and Intimate Partner Aggression (NCT03046836), a randomized phase 2 study. The primary outcome is Change in Alcohol Craving.

2. Clinical Question

3. Trial Design

This was a randomized, double-masked, parallel-group phase 2 trial with a registry enrollment of 200. The two arms were intranasal oxytocin and matching saline placebo. The registry lists the trial status as completed, with a start date of 2017-07-01 and a primary completion date of 2021-04-11. More detail about the sequence generation, concealment of allocation, masking procedures, and the conduct of the trial is not reported in the registry record.

The registry describes the study as a human laboratory paradigm intended to examine alcohol craving and aggression among couples with alcohol use disorder and co-occurring intimate partner aggression. The listed condition is alcohol use. The registry does not report detailed eligibility requirements, participant demographics, or how couples were represented in the allocation and analysis. It therefore cannot be determined from the record whether both members of every couple contributed data to each outcome, or how any within-couple relationship was handled statistically.

The intervention descriptions state that each participant would self-administer 40 international units (IU) of intranasal oxytocin or a matching saline placebo. The record identifies a parallel design, but the timing and adherence details beyond the endpoint timeline are not fully documented. The primary outcome uses measurements around an alcohol cue. A secondary aggression outcome is described as comparing measurements after the cue and during the Taylor Aggression Paradigm (TAP).

The posted results include primary craving summaries for 100 participants in each arm and one secondary aggression comparison with the same arm counts. Although change in cortisol is named among the secondary outcomes, detailed results for cortisol are not reported in the registry record. The registry reports five outcome measures, but does not provide a complete list of all posted measure-level results in the material available for interpretation.

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: One hundred couples (N = 200 individuals) were enrolled using 1:1 randomization. Both partners within a couple were assigned to the same condition (oxytocin or placebo). Inclusion criteria indicated that one or both partners in each couple met DSM-5 criteria for current AUD and endorsed physical intimate partner aggression (IPA i.e., hitting, slapping) that occurred at any point during their current relationship, as assessed by the Revised Conflict Tactics Scale.

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 Change in Alcohol Craving, measured over Participants completed the VAS at 8 timepoints. Outcome measure represents the change in VAS scores between time point 3 (before the alcohol cue) and 4 (after the alcohol cue)..

The primary endpoint is change in subjective alcohol craving measured by a visual analogue scale (VAS). The reported change compares the score at time point 3, before the alcohol cue, with the score at time point 4, immediately after the cue. Participants completed the VAS at eight timepoints during the laboratory session, but this primary endpoint focuses on that specific before-and-after cue contrast.

The VAS is described as a 100mm scale anchored from 0, meaning no craving, to 10, meaning extreme craving. It is intended to capture a participant’s subjective response rather than an objective measure of alcohol consumption. Measuring craving around a cue allows the study to examine the immediate response in the defined laboratory setting. It does not establish how craving behaves in other settings or over longer periods.

The registry reports the outcome as a mean change, with standard error as the measure of dispersion for each arm. The posted arm means are 0.9 for oxytocin and 1.21 for control. The reported mean difference is -0.31, with the direction defined by the oxytocin and control values in the posted comparison. A negative difference indicates that the reported mean change was lower in the oxytocin arm; it does not, without more information about score construction and interpretation, establish a clinically meaningful benefit.

7. Results Posted in the Registry

• Oxytocin: mean 0.90 versus 1.21 on control; difference -0.31 (95% CI -0.64 to 0.02), standardized effect d = -0.26; z-test p = 0.068.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change in Subjective Aggression

• 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 errors.
• Result:
  • Oxytocin: mean 0.31 versus 0.41 on control; difference -0.10 (95% CI -0.36 to 0.16), standardized effect d = -0.11; z-test p = 0.457.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oxytocin and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcome with detailed posted results is change in subjective aggression, measured between the timepoint after the alcohol cue and the timepoint during the Taylor Aggression Paradigm. The reported comparison is uncertain, with an interval that includes zero. Its unadjusted p value does not provide strong evidence against a no-difference model under the analysis used, but it should not be treated as a standalone verdict about the broader question of aggression.

Viewed alongside the primary craving result, the secondary comparison has a point estimate in the same direction, but both estimates have intervals spanning zero. This overall pattern does not establish a consistent treatment effect across outcomes. The registry names change in cortisol as a secondary outcome, but detailed cortisol results are not reported in the registry record. The record also indicates five outcome measures, so the full set of measures and results cannot be reconstructed from the detailed results.

Unadjusted secondary results carry less weight because multiple outcomes create more opportunities for apparently notable findings to arise by chance. In general, multiplicity can be addressed through a prespecified hierarchy, adjustment procedure, or interpretation that treats secondary results as exploratory. Which approach was used for this trial is not reported in the registry record. The listed unadjusted p values should therefore be read as individual comparisons, not as a complete family-wise assessment across the trial’s outcomes.

Secondary outcomes can help describe whether findings extend beyond the primary endpoint, but they do not automatically confirm or contradict it. Their interpretation depends on prior specification, measurement quality, missingness, model choice, and how many comparisons were considered. Those details are not reported in sufficient depth to support a strong cross-outcome conclusion. The pattern is best treated as descriptive and hypothesis-generating rather than as definitive evidence of a shared effect on craving and aggression.

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

• Change in Cortisol
• Change in Subjective Aggression

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous and is summarized using a mean. A mean describes the average recorded change for participants in an arm. The registry also reports standard errors beside the arm means. A standard error describes the statistical precision of an estimated mean; it is not the spread of individual scores. A larger standard error generally indicates less precise estimation, while a smaller one indicates greater precision, conditional on the data and analysis used.

The comparison is a mean difference between the oxytocin and control arms. The posted primary estimate is -0.31. Its sign follows the arm order used in the comparison: the oxytocin mean is compared with the control mean. The negative sign indicates a lower average change in the oxytocin arm. It does not tell whether a lower change is important to participants, nor does it establish the cause of the difference.

A confidence interval gives a range of values that are compatible with the observed data under the assumptions of the method used to calculate it. The primary interval runs from -0.643 to 0.023. Because this range includes zero, the posted result does not exclude a zero difference at the interval’s stated confidence level. The confidence level itself and the method used to construct the interval are not reported in the registry record. In general, an interval is useful for considering both the direction and the precision of an estimate; it should be read alongside the point estimate rather than as a guarantee that the true value lies within the realized interval.

The unadjusted p value for the primary comparison is 0.068. In general, a p value describes how unusual data at least as incompatible with a specified null model would be if that model and the analysis assumptions held. It is not the probability that the null hypothesis is true, and it is not a direct measure of effect size. The registry labels the result unadjusted. Whether the trial’s own analysis used a prespecified threshold, additional covariates, repeated-measures modeling, or adjustments for multiple endpoints is not reported in the registry record.

The trial description indicates repeated VAS measurements across eight timepoints, while the primary endpoint is defined as a change between two of them. Repeated measurements can be analyzed in different ways, including analyzing a prespecified change score or modeling all measurements jointly. The registry’s posted outcome summary gives the contrast and arm-level means, but the full statistical model and treatment of repeated observations are not reported. It is therefore not possible to determine whether the reported analysis used a model that accounted for the complete repeated-measures structure.

Another design feature is that the study involved couples. Outcomes from two members of a couple may be related. In general, correlated observations can make standard errors too small if an analysis treats them as independent when they are not. The registry record does not report whether both members of each couple were enrolled or how any within-couple dependence was addressed. This is an analysis detail that matters when interpreting the reported precision, but the record does not permit a conclusion about whether the issue arose in this trial.

Over-dispersion is a general concern when observed variability exceeds what a statistical model assumes. If a model does not allow for that extra variability, its standard errors and intervals may be too narrow. The outcomes are reported as continuous measures with standard errors, and the registry does not report a model-based variance assumption or evidence of over-dispersion. This concept is relevant to statistical interpretation generally, but no claim can be made that over-dispersion was present in these data.

The comparison’s posted standard errors are 0.12 in each arm. The registry also supplies an estimated pooled standard deviation of 1.2 and a standardized effect estimate of -0.258. These are descriptive statistical summaries. Standardized effects express a difference relative to a measure of variability; they can help compare outcomes measured on different scales, but their interpretation depends on the scale and context. The registry does not describe a clinical threshold for a meaningful VAS change, so the standardized estimate cannot by itself establish practical importance.

For the secondary subjective-aggression measure, the reported means are 0.31 for oxytocin and 0.41 for control, with standard errors of 0.1 and 0.09, respectively. The mean difference is -0.1. Its interval, from -0.364 to 0.164, includes zero, and the unadjusted p value is 0.457. The same general principles apply: the difference estimates the contrast between arm averages, the interval expresses uncertainty, and the p value is not an effect-size measure. The record does not give a full model description for this outcome.

In general, randomization is intended to make treatment groups comparable on average, while masking is intended to reduce the influence of expectations on participants’ responses and assessments. Those design labels do not eliminate every possible source of bias. The registry identifies randomized, double-masked allocation, but detailed implementation, adherence, and analysis methods are not reported in the registry record. Statistical interpretation must therefore distinguish the design features that are listed from procedural details that remain undocumented.

11. Confidence Intervals and Precision

The primary mean difference is -0.31, and its confidence interval extends from -0.643 to 0.023. This interval spans zero, so the posted data do not precisely distinguish a negative difference from no difference or a small positive difference. The point estimate gives one central summary, while the interval shows that substantial uncertainty remains around it. The interval method and confidence level are not reported in the registry record.

The standard errors for the two primary arm means are each 0.12. These quantify uncertainty in the estimated arm averages, not the range of individual participant responses. The estimated pooled standard deviation is 1.2, which describes variability on the outcome scale in the pooled comparison. The registry does not report distributions or other summaries that would show how individual scores were spread, so the standard errors should not be mistaken for participant-level variability.

The secondary aggression estimate is -0.1, with a confidence interval from -0.364 to 0.164. This interval also includes zero and allows for effects in either direction. Its standard errors are 0.1 for oxytocin and 0.09 for control. As with the primary measure, the available summaries do not establish a threshold for clinical importance, and the precision of an estimate is separate from whether a difference matters in practice.

The plotted and tabulated intervals are best read as a range of values consistent with the data under the analysis assumptions, not as a range containing every plausible explanation or as proof of equivalence. An interval that includes zero does not demonstrate that the groups are identical. Conversely, a point estimate away from zero is not conclusive evidence of a real effect. The registry does not report a prespecified equivalence margin or a clinically meaningful difference threshold.

12. Planning a Similar Trial: Sample Size

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

The planning figures give participants per arm for the continuous-outcome comparisons; they are not total event counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is expressed as a stated fraction of the observed effect. The registry’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm in the planning illustration for a design that would have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the model assumptions held. The 90% power column uses a higher target probability of detecting that specified effect. These are prospective planning quantities, not measures of what happened in the completed trial.

For the primary outcome, planning for 100% of the observed effect gives 236 participants per arm for 80% power and 315 participants per arm for 90% power. Planning for 75% of the observed effect gives 419 participants per arm for 80% power and 560 participants per arm for 90% power. Planning for 50% of the observed effect gives 941 participants per arm for 80% power and 1,260 participants per arm for 90% power. The smaller assumed effects require more participants because a smaller difference is harder to distinguish from random variation under the same assumptions.

The registry reports 100 participants in each arm for the primary result. The planning figures are not observed power and should not be used to infer the probability that the trial’s result is true or false. They are illustrations based on the observed effect, which may itself be uncertain. The trial’s own design assumptions, targeted effect, and original planned sample size calculation are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -0.310; pooled standard deviation σ = 1.200.
2. n = 2 × (1.96 + 0.842)² × 1.200² / -0.310² = 235.2, rounded up to 236 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 <- -0.31                      # observed difference in means
sigma <- 1.2                     # 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(3046836)
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 = 236 (80% power), 315 (90% power)
 75% of observed effect: n per arm = 419 (80% power), 560 (90% power)
 50% of observed effect: n per arm = 941 (80% power), 1,260 (90% power)
power.t.test: 236.2 
Simulated power at n = 236 per arm: 0.796 (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 reports an unadjusted p value for the primary comparison and for the detailed secondary aggression comparison. It does not report whether the trial prespecified a family of hypotheses, a hierarchy of primary and secondary tests, or a statistical adjustment for evaluating multiple outcomes. The listed outcomes include change in cortisol and change in subjective aggression, and the record reports five outcome measures. Without a complete analysis plan and results for every outcome, the extent of multiplicity and any intended control of false-positive findings cannot be assessed.

Missing-data handling is also not reported in the registry record. The posted arm counts are 100 participants per arm, but the record does not clarify whether those counts represent randomized participants, participants with available endpoint data, or participants included after exclusions. It does not report the amount or pattern of missingness, reasons for missing measurements, or any imputation or sensitivity analysis. These omissions limit assessment of whether the estimates could be affected by incomplete outcome data.

The analysis population is not reported. The registry does not say whether results follow an intention-to-treat approach, include only participants who completed the protocol, or use another defined population. It also does not describe how adherence, protocol deviations, or participant withdrawal were handled. Consequently, the relationship between randomization and the analyzed groups cannot be fully evaluated from the posted record.

Because the study is described as involving couples, the statistical treatment of paired or clustered participant data is relevant. The record does not state whether both members of a couple contributed observations, whether couple-level dependence was modeled, or whether analyses used a participant-level or couple-level unit. No conclusion about the effect of such dependence can be drawn without that information.

These gaps do not change the numerical summaries, but they narrow what can be concluded from them. A fuller statistical analysis plan, participant flow information, and outcome-level missingness details would be needed to assess multiplicity, analysis population, and robustness to missing data.

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 1% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports no serious adverse events among 100 participants at risk in either the oxytocin or control arm. It also reports no deaths in either arm. These are the serious-event figures recorded for the trial, not evidence that rare events could not occur or that all possible harms were ruled out.

For other adverse events, the registry reports none among 100 participants at risk in the oxytocin arm and 6 among 100 participants at risk in the control arm. These counts should be read as descriptive registry summaries. The record does not provide event types, severity details for the non-serious events, timing, attribution, or the methods used to collect and classify adverse events. No causal conclusion about differences between the arms follows from these counts alone.

Safety comparisons can be affected by the duration and completeness of follow-up, the definitions used for event categories, and the way events were solicited and recorded. Those details are not reported in the registry record. The absence of recorded serious events in these groups is therefore a statement about the posted counts, not a guarantee about safety in other populations or settings.

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

The primary result estimates the average difference in change in alcohol craving between participants assigned to intranasal oxytocin and those assigned to matching saline placebo, over the specified interval around an alcohol cue. The posted estimate is -0.31, with a confidence interval from -0.643 to 0.023. It indicates a lower mean change in the oxytocin arm in this sample, while the interval includes zero and leaves uncertainty about the direction and size of the underlying difference.

The estimate does not establish that oxytocin caused a change in craving, nor does the interval establish that the groups are equivalent. The registry does not report a clinically meaningful threshold for the VAS or a decision rule for interpreting this magnitude. The score is a subjective laboratory measure at specified timepoints; it is not a direct measure of drinking behavior, longer-term alcohol use, or outcomes in everyday life.

The secondary aggression estimate is also uncertain, and the detailed cortisol results are not reported in the registry record. These outcomes do not supply a basis for a broad conclusion about aggression or cortisol effects. Interpretation is further limited by the absence of reported analysis-plan details, missing-data handling, participant flow, and information about how any dependence between members of couples was addressed.

The trial’s randomized, double-masked, parallel-group design is relevant to the intended comparison, but design labels alone do not resolve those reporting gaps. The registry record gives useful outcome summaries, yet it does not provide enough detail to determine how robust the estimates are to alternative analysis choices or whether all planned outcomes are represented.

Accordingly, the posted results are best understood as estimates from a laboratory trial with appreciable uncertainty. They neither demonstrate a clinically important effect nor prove an absence of one. They should not be generalized to other outcomes, populations, or settings beyond what the registry describes.

17. Why This Trial Matters Statistically

This trial raises a statistically useful question because it measures two subjective responses in a defined laboratory context: alcohol craving around an alcohol cue and aggression during a paradigm. The design is randomized, double-masked, and parallel-group, and the registry posts arm-level means, standard errors, mean differences, confidence intervals, and unadjusted p values. Those elements allow readers to assess the estimated contrast and its uncertainty rather than relying only on a verbal claim.

The results also illustrate why effect estimates and confidence intervals matter together. A negative point estimate may suggest a direction in the observed sample, but an interval that includes zero leaves meaningful uncertainty. The same principle applies to secondary outcomes: a directionally similar estimate does not constitute independent confirmation when its precision is limited and multiple outcomes may have been considered.

The study further highlights the importance of registry reporting. Key details about the full statistical plan, sample-size justification, missing data, analysis populations, multiplicity, and the treatment of couples’ data are not reported in the registry record. Without these details, readers cannot fully evaluate the analysis decisions behind the estimates or the extent to which the published summaries represent all randomized participants and planned outcomes.

Finally, the planning illustration demonstrates how target effect size and desired power influence the number of participants needed under stated assumptions. It is a planning aid, not a retrospective score of trial success. Taken together, the record supports a careful reading centered on uncertainty, design context, and transparency about what remains undocumented.

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 registry does not report detailed participant characteristics, eligibility criteria, recruitment procedures, or the composition of couples enrolled. This limits assessment of how closely the study population corresponds to the broad description of couples with alcohol use disorder and co-occurring intimate partner aggression. The listed condition is alcohol use, and the population field for the primary outcome is blank.

Although the study is identified as randomized and double-masked, the registry does not describe how allocation was generated or concealed, how masking was maintained, or whether masking was assessed. These omissions prevent a detailed appraisal of implementation. The record also does not give adherence, protocol deviation, or withdrawal information.

The primary endpoint is a specific change between two VAS timepoints in a laboratory session. The registry does not report a clinically important difference threshold, a full account of the statistical model, or whether the repeated measurements were analyzed jointly or as a change score. It also does not report how any within-couple correlation was handled, despite describing a study of couples.

Additional limitations concern reporting of outcomes and analysis decisions. Detailed cortisol results are not reported in the registry record, even though change in cortisol is named as a secondary outcome. The full statistical plan, multiplicity approach, analysis population, missing-data methods, and original sample-size justification are also not reported. These gaps make it difficult to judge the completeness and robustness of the posted estimates.

Finally, the outcomes are laboratory measures at defined timepoints. The registry record does not establish how these measures relate to longer-term behavior or outcomes outside the study setting. These limitations constrain interpretation of the reported numerical comparisons; they do not, by themselves, determine what the unreported analyses or outcomes would show.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Oxytocin, Alcohol Craving, and Intimate Partner Aggression — NCT03046836.
• Registry record last updated 2022-05-09; status last verified 2022-05.
• Results first posted 2022-05-09.
• 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 a completed, randomized, double-masked, parallel-group phase 2 trial comparing intranasal oxytocin with matching saline placebo. The stated enrollment is 200, and the posted primary craving results include 100 participants per arm. The primary endpoint is change in VAS craving from before to immediately after an alcohol cue.

The posted primary mean difference is -0.31, with a confidence interval from -0.643 to 0.023 and an unadjusted p value of 0.068. The detailed secondary result concerns subjective aggression and also has an interval that includes zero. Detailed cortisol results, the trial’s full statistical plan, missing-data methods, analysis populations, and original sample-size assumptions are not reported in the registry record.

The numerical results should be interpreted as uncertain laboratory estimates, with limits on broader conclusions from the available reporting.