Disulfiram for Cocaine Abuse: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Disulfiram for Cocaine Abuse (NCT00395850), a randomized phase 2 study. The primary outcome is Cocaine Use Over Time.

2. Clinical Question

3. Trial Design

The registry identifies NCT00395850 as a randomized, quadruple-masked, parallel-group phase 2 trial of disulfiram for cocaine dependence. The record lists University of Arkansas as the sponsor and an enrollment of 118. The brief summary describes a planned 14-week study for up to 160 people aged 18-65 years; the registry enrollment and the intended maximum in the summary are different types of figures and should not be conflated.

Four assignments are listed: placebo, disulfiram 250 mg/day, disulfiram 375 mg/day and disulfiram 500 mg/day. The brief summary says participants were stratified by DBH genotype before random assignment. It also describes methadone stabilization during the first 2 weeks for participants who were opioid dependent, with cocaine use assessed at baseline. Methadone was continued where relevant during the subsequent disulfiram or placebo phase.

The primary outcome concerned urine toxicology results collected thrice weekly for 12 weeks. The analysis population for this measure is described as participants who remained long enough for assessments at two time points during the disulfiram phase. The posted outcome groups have different participant counts, and the registry's general enrollment figure should not be read as the analysis count for each measure.

The registry marks the study completed. It reports retention as a secondary outcome over 14 weeks. Further details about implementation, including how masking was maintained and whether allocation concealment procedures were used, are not reported in the registry record. Nor is a detailed protocol or a full account of participant flow reported in the registry record.

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: Participants underwent either a two-week induction onto methadone (if opioid dependent) or a two-week baseline period prior to randomization to the treatment arms and receiving medication starting in week 3. Those receiving at \>1 dose of medication and completing assessments at at least 2 time points during week 3 were include in the analyses.

Pre-randomization Baseline/Induction

Reasons for not completing this period:

Randomization to Disulfiram/ Pre-admin

Reasons for not completing this period:

Disulfiram/Placebo Treatment

Analysis population for the primary outcome, as defined in the registry: number is based on those who participated long enough to have assessments completed at two time points during the disulfiram phase

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 Cocaine Use Over Time, measured over thrice weekly for 12 weeks.

The primary endpoint was cocaine use over time, expressed as the slope in change in the probability of a cocaine-positive urine toxicology result per day. Urine results were dichotomous: positive or negative for cocaine or its metabolite. The record says urine testing took place thrice weekly during the 12-week disulfiram phase, and that repeated-measures generalized linear models with a binomial distribution were used to estimate the slopes. This is a repeated-measures logistic regression approach.

A slope represents the direction and rate of change in the modeled probability over time, rather than a simple count of positive samples or a single end-of-study measurement. In general, repeated observations can show whether the probability appears to rise or fall during follow-up while accounting for the fact that measurements come from the same participant. The registry record does not report the precise model specification, covariates, or handling of observations that were not collected.

The stated endpoint is clinically relevant to the trial question because it uses repeated objective urine assessments to track cocaine-positive results during treatment. It does not, by itself, describe every aspect of cocaine use, treatment engagement, or functioning. The endpoint population is restricted to those with assessments at two time points during the disulfiram phase, so it is not necessarily identical to everyone enrolled or assigned.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

Repeated measurements require a method that recognizes that observations from the same participant are related. A participant's urine result at one visit is not generally independent of that participant's result at another visit. In general, treating all visits as independent can make uncertainty appear smaller than it is. Repeated-measures models are designed to account for the structure of measurements over time, although the exact approach and assumptions matter.

What does the primary slope represent?

The registry describes the primary endpoint as change in the probability of a cocaine-positive urine result per day. A slope condenses the time pattern into a direction and rate of change under the fitted model. It is different from the proportion of all tests that were positive, and different from the chance of a positive urine result at one particular time. The posted arm values are 0.01 for placebo, 0.007 for disulfiram 250, -0.01 for disulfiram 375 and 0.007 for disulfiram 500. Since the endpoint is described as a change in probability per day, these should be read as modeled slopes, not as standalone risk estimates.

The model is described as a repeated-measures generalized linear model with a binomial distribution, also called repeated-measures logistic regression. In general, a binomial model is appropriate for a binary outcome such as positive versus negative. Logistic regression models the log odds of the outcome, and a model can use time to estimate whether those odds change. The registry describes the endpoint in probability terms, but it does not report enough detail to determine the precise scale on which the reported analysis value of -1.02 is expressed. It is therefore not appropriate to translate that value into a probability difference without further model details.

What does the reported p-value establish?

The sponsor's analysis reports a value of -1.02 and p < 0.05 for the comparison of the three active-dose groups with placebo. In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions were correct. It is not the probability that the null hypothesis is true, and it does not measure the magnitude of an effect. The registry does not state the exact null contrast, test statistic definition, or confidence interval for this primary analysis. That limits the precision with which the result can be interpreted.

In a multi-arm trial, an overall or combined test and comparisons of each active dose with placebo answer different questions. An overall test can address whether the set of groups differs under a particular model, while separate contrasts assess specific dose comparisons. The registry lists the groups included in the sponsor's analysis but does not provide separate primary p-values or confidence intervals for every dose-versus-placebo contrast. Consequently, the reported result should not be treated as evidence that each dose individually had the same pattern or strength of association.

Why can over-dispersion matter?

In general, over-dispersion occurs when binary outcomes vary more than the assumed model allows. If it is present and not handled appropriately, standard errors and tests may be unreliable. Repeated outcomes can also have correlations that require appropriate modeling. The registry record identifies a binomial repeated-measures model but does not report an over-dispersion assessment, the correlation structure, or sensitivity analyses. Those details are not reported in the registry record, so the reader cannot assess how these features were addressed.

How should recalculated comparisons be read?

The retention recalculations use posted group means and standard deviations to estimate unadjusted pairwise mean differences. A confidence interval in general conveys the range of effect estimates compatible with the data and assumptions; when it crosses zero for a mean difference, the data do not clearly distinguish the estimated difference from no difference under that calculation. The recalculations are not adjusted for other variables or for multiple comparisons. They should be treated as descriptive checks, not as replacements for the sponsor's analysis.

The planning illustrations use the observed retention effect as a planning input under stated assumptions, including equal allocation, a two-sided significance level of 0.05 and a normal approximation. They are hypothetical sample-size calculations, not observed power and not evidence about the design that the investigators actually used. The trial's sample-size justification and design assumptions are not reported in the registry record. The planning values therefore should not be mistaken for a retrospective claim that the study had or lacked a particular level of power.

What information is missing?

Important details for evaluating the primary model are not reported in the registry record, including the prespecified estimand, exact contrast, covariate adjustment, model diagnostics, missing-data approach and sensitivity analyses. In general, an estimand defines the treatment effect a study intends to estimate, including how intercurrent events and missing outcomes are handled. Without that definition and the full analysis plan, the sponsor's reported result is best understood at the level of the registry's description rather than reconstructed in greater detail.

10. Analyses Reported by the Sponsor

The registry reports the sponsor's primary analysis as repeated-measures logistic regression, with the three disulfiram groups compared with placebo. The reported value is -1.02, with p < 0.05; a confidence interval is not reported in the registry record. The record does not clarify the precise scale or contrast represented by that value. It should therefore be reported as the sponsor's stated result, without translating it into an unreported effect measure.

The arm-specific slopes are descriptive estimates for the four groups, while the sponsor's result is a model-based analysis involving the active groups and placebo. They are related to the same primary endpoint but do not present the same statistical quantity. The posted information does not permit a full independent reconstruction of the sponsor's primary model, so no recalculated primary test is offered as a substitute.

For retention, the sponsor reports a two-sided t-test analysis across the four groups, with a mean difference of 1.5 and p < 0.05. The registry does not identify that result as a particular pairwise contrast. Recalculations from posted summary statistics address pairwise comparisons for some active-dose groups and are unadjusted; they do not reproduce the sponsor's four-group analysis. The registry's discrepancy indicator is false, but that does not make these different analyses interchangeable. Their scope and methods should remain distinct when reading the results.

11. Multiplicity, Missing Data and Analysis Populations

The trial has multiple randomized groups, and the primary report describes a comparison of three disulfiram doses with placebo. The record does not report whether the primary inference used a single overall test, a planned family of dose-specific contrasts, or a dose-response test. It also does not describe an adjustment for multiple primary contrasts. These details are not reported in the registry record, so the protection against false-positive findings across comparisons cannot be evaluated.

Multiplicity also applies across outcomes and analyses. Retention is posted as a secondary outcome, and the registry gives a sponsor analysis as well as summary statistics from which some pairwise comparisons are recalculated. No analysis hierarchy, family-wise error procedure, false-discovery procedure, or distinction between confirmatory and exploratory secondary results is reported in the registry record. In general, if many hypotheses are tested, unadjusted p-values can overstate the strength of evidence when interpreted as a collection.

The primary outcome population is defined as participants who had completed assessments at two time points during the disulfiram phase. This eligibility condition means the analysis is not automatically an intention-to-treat analysis of everyone randomized. The record does not report how many randomized participants lacked the required assessments, how missing urine results were handled, whether participants were analyzed according to assignment, or whether a sensitivity analysis evaluated alternative assumptions about missing observations. These matters are not reported in the registry record.

More generally, missingness can be related to treatment, ongoing cocaine use, health, or other factors. If participants with missing measurements differ systematically from those with observed measurements, an analysis limited to available observations may not represent the randomized groups as intended. This is a general concern, not evidence that a particular bias occurred in this trial. The posted description does not give enough information to judge the likely direction or magnitude of any such effect.

The sample-size justification, interim analyses, stopping rules and full statistical analysis plan are not reported in the registry record. Without these details, the reader cannot determine whether the reported analyses followed a prespecified plan or whether decisions made during the study could have influenced the inferences.

12. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: suicidal ideation (5.0%), acute copd exacerbation (4.3%), spinal abcess (4.2%).

The registry posts serious adverse event counts for each group among those described as at risk. The reported counts are 1 serious event in placebo, 1 in disulfiram 250, 1 in disulfiram 375 and 0 in disulfiram 500. The corresponding at-risk counts are 20, 23, 24 and 21. These figures are counts, not estimates of comparative risk, and the registry does not report deaths in these groups.

Other adverse events are listed for the same at-risk groups: 8 in placebo, 12 in disulfiram 250, 10 in disulfiram 375 and 11 in disulfiram 500. The record also lists suicidal ideation at 5.0%, acute COPD exacerbation at 4.3% and spinal abcess at 4.2% among top serious-event terms. These terms and percentages are registry entries; the record does not provide enough context to establish which group-specific patterns underlie each percentage.

In general, safety comparisons require attention to event definitions, observation time, exposure, severity, and uncertainty, as well as counts. The posted figures are too limited to establish that event rates differ between groups or to assess rare harms precisely. Serious and other adverse events should be read as descriptive registry data, not as a complete account of safety.

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

The primary registry result describes a sponsor-reported repeated-measures analysis of cocaine-positive urine tests over time. The reported p-value is below 0.05, but the registry does not give a confidence interval or a fully specified contrast for the reported value. The separate arm slopes vary in direction, and the record does not supply dose-specific primary tests that would show which individual groups differ from placebo. These features limit the strength and specificity of conclusions that can be drawn from the posted result.

The endpoint is a modeled time trend in urine toxicology, not a direct summary of all cocaine use or all consequences of cocaine dependence. It does not answer every question about sustained treatment engagement, functioning, or safety. Retention was also reported, but it measures a different outcome and its sponsor analysis does not identify a specific pairwise contrast in the registry record.

In general, statistical significance does not establish that an effect is large or important to patients. A p-value does not provide the probability that a treatment is beneficial, and without a confidence interval the precision of the estimated primary effect is difficult to judge. The record's missing methodological details also prevent a full assessment of the assumptions behind the reported analysis.

The study was randomized and masked according to the registry, features intended in general to reduce some sources of bias. They do not eliminate uncertainty from missing outcomes, limited precision, incomplete reporting, or analysis choices. The registry identifies an enrolled population and a particular treatment setting, including methadone stabilization for some opioid-dependent participants. Results should be interpreted within that study context rather than automatically generalized to other populations or treatment settings.

These results do not establish that any disulfiram dose should or should not be used. They describe the estimates and analyses posted in the registry, together with substantial limits on interpretation. Clinical decisions require evidence beyond this registry record and consideration of individual circumstances; the statistical findings alone are not medical advice.

14. Why This Trial Matters Statistically

This trial is statistically informative because it combines a randomized multi-arm design with a repeated binary outcome measured over time. That combination raises questions beyond a simple comparison of group averages: analysis must account for within-participant correlation, define a treatment contrast, and make clear how incomplete follow-up is handled. The registry identifies a repeated-measures logistic-regression approach, but it does not provide enough detail to evaluate all of those choices.

Several doses can help investigate whether patterns vary across treatment assignments, but multiple groups also create multiple possible comparisons. An overall test, dose-specific comparisons and a dose-response analysis are distinct questions. The registry's report of a combined active-group comparison should not be mistaken for a complete account of each dose's result. Missing contrast details illustrate why transparent reporting of estimands, model scales and uncertainty is essential.

The endpoint also illustrates the difference between a repeated binary outcome and a simple event count. A slope captures the modeled trajectory rather than the total number of positive tests. This can be useful when change over time is central to the research question, but interpretation depends on the model and the timing and completeness of measurements. The record's requirement for at least two time points makes analysis-population definitions particularly relevant.

Finally, the coexistence of sponsor analyses and recalculations from summary statistics shows why statistical results must be compared according to what each analysis actually tests. A summary-statistic recalculation can provide a limited descriptive check, but it cannot reproduce a model-based analysis without the underlying data and specification. For researchers, the record highlights the value of reporting confidence intervals, analysis populations, missing-data methods, multiplicity plans and clearly identified contrasts alongside p-values.

15. Limitations

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

Several limitations are specific to the available record. Although the brief summary describes a planned study for up to 160 people, the registry lists enrollment of 118. The reported outcome groups have smaller counts, and the primary outcome description restricts analysis to participants with assessments at two time points. The record does not provide a participant-flow account that explains the difference between enrollment and the outcome populations.

The primary results lack confidence intervals and dose-specific inferential comparisons. The sponsor's reported value and p-value are not accompanied by enough detail to establish the exact contrast or scale. The individual slope estimates are available, but they do not by themselves quantify uncertainty. This makes it difficult to judge whether the apparent differences among group estimates are precise or compatible with a broad range of effects.

The registry does not report the full statistical model specification, covariate adjustment, missing-data method, diagnostics, sensitivity analyses, sample-size justification, interim analyses or statistical analysis plan. It also does not describe how DBH genotype stratification was incorporated into the analysis or report genotype-specific outcomes. These items are not reported in the registry record, and their absence prevents deeper evaluation rather than proving that the investigators did not address them.

The primary endpoint is a repeated urine measure, but the record does not report adherence to the testing schedule or how missed visits were handled. Nor does it provide a detailed account of exposure or treatment discontinuation by group. The retention outcome is relevant to follow-up but cannot resolve those uncertainties on its own.

Finally, the adverse-event entries are limited to registry counts and listed terms. They do not provide enough context for detailed comparative safety analysis. These limitations mean that the posted results are best treated as an incomplete account of a completed trial rather than a full clinical or statistical report.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Disulfiram for Cocaine Abuse — NCT00395850.
• Registry record last updated 2013-11-13; status last verified 2013-09.
• Results first posted 2013-11-13.
• 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.

19. Record Summary

NCT00395850 is a completed, randomized, quadruple-masked, parallel-group phase 2 trial sponsored by University of Arkansas. The registry lists enrollment of 118 and four assignments: placebo and disulfiram at 250 mg/day, 375 mg/day or 500 mg/day. The brief summary describes a 14-week study and methadone stabilization for participants who were opioid dependent.

The primary outcome was the slope in the probability of cocaine-positive urine tests over time, measured thrice weekly during the 12-week disulfiram phase. The sponsor reports a repeated-measures logistic-regression result of -1.02 with p < 0.05, but no confidence interval is reported in the registry record. Retention was posted as a secondary outcome. The record does not provide enough detail to fully assess the primary contrast, missing-data handling, multiplicity or analysis precision.