Did Disulfiram Reduce Cocaine-Positive Urine Tests? What a 49-Patient Methadone Trial Actually Found

Answer first: A small randomized, double-blind study did not establish that any of three disulfiram doses produced a statistically significant decline in cocaine-positive urine findings within its own treatment group. Compared with placebo, however, the 250 mg/day and 375 mg/day arms had significantly different trends over the study period (p < .015 and p = .015, respectively). The reason matters: the placebo group’s cocaine-positive urine trend increased, while the two disulfiram slopes were numerically negative but did not significantly depart from zero. The 500 mg/day comparison was nonsignificant. This supports a narrow, preliminary finding about group trajectories—not proof of sustained abstinence, a particular person’s dose, or an individual forensic blood concentration.

The original evidence comes from Alison H. Oliveto, Janette McGaugh, Mohit P. Chopra, Jeff Thostenson, and Michael J. Mancino (2025), A randomized clinical trial of disulfiram at higher doses for the treatment of cocaine use disorder among methadone-stabilized patients, Journal of Psychiatric Research 186:387–395, original empirical study DOI. Investigators enrolled 53 people in the opioid-dependent trial, while 49 actually received assigned study medication and contributed the principal analyzed clinical cohort. Repeated urine specimens and repeated treatment visits did not increase the number of independent patients.

What question did this randomized clinical trial answer?

Its central question was whether adding daily oral disulfiram at 250, 375, or 500 mg to a supervised methadone treatment program changed the course of cocaine-use indicators compared with placebo. Each participant also received individual cognitive-behavioral therapy. Researchers followed the pattern of positive urine screens for benzoylecgonine, a cocaine metabolite, over weeks rather than administer a known research dose of cocaine and measure subsequent blood pharmacokinetics. That difference defines both the study’s clinical value and its forensic limits.

A treatment outcome and an analytical toxicology result must not be collapsed into a single proposition. A trajectory of clinic urine screens describes how often samples crossed the laboratory’s positivity criterion at scheduled visits. It does not automatically describe cocaine consumption in grams, the number of discrete use episodes, or the chemical concentration in venous blood. Nor can a favorable contrast with a worsening placebo trajectory, by itself, establish a robust absolute decrease within a medication arm. The study’s results are especially informative because the authors reported both kinds of comparison rather than treating them as interchangeable.

Who was recruited, randomized, and actually analyzed?

The publication describes 53 enrolled participants with cocaine and opioid dependence in the main study, of whom four never received their allocated intervention. The resulting 49 treated participants were allocated as follows: 13 received placebo, 13 received disulfiram 250 mg/day, 13 received 375 mg/day, and 10 received 500 mg/day. These numbers refer to actual human participants, not the number of urine containers or repeated observations. The trial’s recruitment history also included a separate group with cocaine dependence but without opioid dependence; the researchers explicitly excluded that group from this reported analysis because procedures differed. Its members must not be silently merged into the 49-person cohort.

The participants were seeking treatment in central Arkansas under stringent eligibility conditions. Current alcohol physiological dependence, several significant medical and psychiatric disorders, certain medication exposures, and several cardiovascular and liver-related conditions were exclusionary. Their average age was approximately 37 years, and the groups were broadly comparable on measured baseline characteristics. Randomization improves interpretation within this selected cohort, but it does not make the study representative of every person encountered in a forensic case, emergency department, highway investigation, correctional setting, or substance-use treatment program.

How did methadone treatment and the three disulfiram doses differ?

The experiment lasted 14 weeks. During the first two weeks, participants were stabilized onto methadone; the research protocol describes starting at 25 mg/day, increasing toward 60 mg/day, and permitting clinical adjustment thereafter. From week three through week fourteen, the blinded assigned treatment was placebo or oral disulfiram 250, 375, or 500 mg/day. On clinic days, crushed active tablets or matched placebo were suspended in the methadone solution. Participants attended the clinic six days each week and received take-home study medication for Sunday. Weekly one-hour individual cognitive-behavioral therapy accompanied all arms.

The disulfiram dose is a documented administered treatment assignment, not a quantified blood level. Milligrams swallowed cannot be converted to a person’s plasma disulfiram, serum metabolite, or cocaine concentration by treating a clinic urine screen as a pharmacokinetic assay. Methadone was a common co-treatment, rather than an independently randomized comparator against no methadone. Differences among groups therefore concern disulfiram added to this clinical setting; they do not establish the effects of disulfiram alone in people outside methadone care.

Which specimen and chemical did the investigators test?

The drug-use endpoint came from supervised urine collection three times per week. Researchers tested for the presence of benzoylecgonine, a major cocaine metabolite, and other designated drugs using a Hitachi 717 automated analyzer, with a reported urine decision cutoff of 300 ng/mL. The publication uses the proportion of cocaine-metabolite-positive urine screens to model treatment outcomes. Although the cutoff carries concentration units, the main outcome was a positive-versus-negative result and its trend, not a reported individual quantitative concentration series for cocaine in urine.

Cocaine and benzoylecgonine are different chemical analytes. The specified positive urine screen should not be rewritten as confirmed parent cocaine in venous whole blood, measured cocaethylene, or validated time since administration. The paper did not describe a confirmatory GC–MS or LC–MS/MS cocaine concentration series tied to each urine screen. The assay’s 300 ng/mL urine decision cutoff is a clinic classification point, not a legal blood-driving threshold, universal proof of recent cocaine ingestion within a fixed interval, or a chemical identity statement that applies to unrelated methods. For background, see the published guidance on different toxicology specimen matrices.

How should an analyst count repeated testing?

Each of the 49 people was observed repeatedly during the clinical program. The schedule offered up to 39 urine-sampling opportunities per person in the relevant follow-up window. Those are repeated within-person observations, with possible correlation from one visit to the next. They must not be treated as 49 multiplied by 39 newly recruited independent individuals. The analysis used a hierarchical longitudinal modeling approach specifically intended to account for repeated observations and unbalanced follow-up.

The reporting unit also changes across the paper. A percentage of collected urine specimens that screened positive is not the same denominator as the number of unique people who had any positive sample. A responder defined by comparing week-two and week-fourteen percentages is a separate person-level, post hoc classification. An adverse-event episode count is another different denominator. Keeping these quantities separate prevents the sort of false precision that can arise when a forensic report turns observations about visits into assertions about unique people or events.

What were the primary modeled cocaine-positive urine trends?

The key analysis began from the last baseline urine measurement in week two and continued through week fourteen. Placebo had a reported positive modeled slope of +0.064. The 250-mg arm had a slope of −0.038, the 375-mg arm −0.033, and the 500-mg arm +0.003. The source gives these hierarchical-model estimates; they should be reported as its modeled slope coefficients, not casually relabeled as percentages or percentage points per day without a separately validated unit definition. The plotted points and model curves are not individual toxicology reports.

The 250-mg and 375-mg contrasts with placebo were statistically significant, with source-reported t = −2.45, p < .015 and t = −2.44, p = .015. But their slopes tested separately against a horizontal zero-slope reference yielded p > .15 and p > .17. The placebo slope differed significantly from horizontal (p < .05). This is the crucial comparison structure: the medication slopes can differ from a rising placebo group without demonstrating an independently significant absolute decline in those medication arms.

Evidence table 1: between-arm differences versus within-arm change

Nothing in this table establishes that the 250-mg or 375-mg arms became cocaine-abstinent. The smaller arm sizes and noisy measurements preclude confident statements about an individual patient’s likely response. Likewise, the nonsignificant 500-mg contrast should not be overread as proof of treatment equivalence, the impossibility of benefit, or a dose-related safety boundary in all patients.

Was cocaine use already different before disulfiram started?

At the second study week, before assigned disulfiram was given, the percentage of cocaine-positive urine screens was reported between 28.21 ± 11.23% for placebo and 47.22 ± 13.27% for the 500-mg group. These values were presented as means with accompanying uncertainty in the original results. The across-arm comparison was nonsignificant (p > .43). The final week-two screen chosen as baseline for the longitudinal analysis was also not significantly different between groups (source-reported Fisher test p > .35).

A nonsignificant baseline test does not demonstrate identical starting conditions. With groups as small as ten to thirteen people, clinically meaningful imbalance can remain hard to detect. The randomization and within-person longitudinal framework are relevant, but the modest sample and varied observation counts still constrain the certainty of later differences. A responsible summary preserves the baseline data as context rather than implying that the trial created four numerically identical cocaine-use groups.

Why does significance relative to placebo not prove a reduction within the treated arm?

Imagine two longitudinal trajectories. One climbs over time and the other remains approximately level. Their difference in slopes can be statistically detectable even though the second trajectory does not show a statistically demonstrable downward movement on its own. The disulfiram report closely resembles that situation. The placebo trajectory rose; the 250-mg and 375-mg trajectories were numerically downward but compatible with horizontal slopes under the authors’ within-arm tests.

This distinction is not a technicality about language. A headline saying disulfiram “lowered urine cocaine levels” would claim a chemical measurement that was not made and a within-group decline that the statistical tests did not establish. Saying that certain medication arms avoided the same modeled increase observed in placebo is closer to what the study directly supports, subject to sample size, follow-up, and modeling uncertainty. The 500-mg arm failed to demonstrate even that between-arm slope difference in the reported analysis.

Did the responder counts confirm a significant abstinence benefit?

No. The investigators added an exploratory responder analysis after specifying the principal longitudinal method. Among completers, responder counts were placebo 0/10, 250 mg 1/7, 375 mg 1/4, and 500 mg 2/4. The four-group comparison was p = .088, above the specified .05 threshold. With only four completers in each of the higher-dose arms, a single person’s status changes the corresponding percentage by 25 percentage points. Impressive-looking percentages from such tiny groups are unstable estimates.

When the analysis instead included all people who started week three and classified noncompleters as nonresponders, the counts were 0/13, 1/13, 1/13, and 2/10 for placebo through 500 mg. That comparison was also nonsignificant (p > .42). These choices yield different denominators and meanings. The study’s responder was a person with a lower proportion of positive urine screens at week fourteen compared with week two, not necessarily somebody who had no cocaine exposure, no positive urine specimen, or a documented clinical remission.

How extensive were loss to follow-up and missing urine samples?

Twenty-four of 49 participants receiving the assigned medication did not finish the protocol. The authors reported no significant medication-group difference in retention (log-rank statistic 5.384, p = .1457). They also reported that the average fraction of scheduled urine specimens missing ranged from 21.0 ± 31.9% in placebo to 42.6 ± 33.6% in the 375-mg arm; the between-group comparison was nonsignificant (p > .20). A missing urine is not a chemically observed negative or positive drug test.

The hierarchical model used available measurements despite unbalanced repeated visits. That is a defensible design choice and more informative than simply pretending all missed collections happened. It does not, however, guarantee that loss to follow-up was unrelated to current drug use, side effects, housing, transportation, motivation, or treatment acceptability. The study therefore provides evidence about observed and modeled treatment trajectories under its methods, not a fully verified weekly exposure record for everyone originally enrolled.

Evidence table 2: endpoints that limit an overbroad treatment claim

The results above do not establish that cardiovascular risk was absent or that all doses had the same risk. They simply state which comparisons the original investigators tested and did not reject. The adverse-event analysis records a different kind of evidence from the urine outcome; it cannot be substituted for a chemical determination of drug concentration or for an adjudication of event causation.

Did the study show differences in anxiety, depression, or vital signs?

Hamilton Anxiety Scale scores declined across study time overall (t = −3.58, p < .001), but the medication-by-time interactions for anxiety did not reach significance (p > .08). For Hamilton Depression scores, the placebo slope was significant (p < .004) and the 500-mg slope was significant (p < .03), while the 250-mg (p > .27) and 375-mg (p > .86) slopes were not. One comparison indicated that placebo depression scores decreased more quickly than those in the 375-mg group (p < .04). These are symptom-rating findings, not evidence of biochemical cocaine concentrations or individual psychiatric causation.

For routinely measured pulse and blood pressure, the group-by-week comparisons were nonsignificant, although the systolic blood-pressure result approached the conventional boundary (p = .0575). No significant finding in this selected, relatively small cohort should be used as a general assurance about rare cardiovascular reactions in excluded higher-risk individuals. Conversely, an observed blood-pressure or anxiety symptom in one participant is not automatically caused by cocaine, disulfiram, or methadone without an appropriate contemporaneous evaluation.

What safety outcomes were actually recorded?

The investigators documented 154 adverse-event episodes during the trial, of which 72 were judged at least possibly study-related before treatment codes were opened. These are episode counts, not the number of patients with an adverse event. Four individuals were administratively discharged because of events the team considered possibly related: recurring nausea and vomiting in the setting of continued alcohol use, syncope, auditory hallucinations, and cocaine-associated paranoia. One spinal-abscess event was considered serious but unrelated to study participation. The authors reported no deaths.

The proportion of participants reporting at least one study-related event did not differ significantly among arms. Reported gastrointestinal complaints warrant attention, but the publication does not offer enough precision to rank every clinical hazard across broad populations. Of special forensic importance, a reported adverse event is not necessarily a confirmed drug mechanism. Serious-event attribution calls for chronological medical records, medication exposures, toxicology in the actual relevant specimen, and other plausible causes—not a numerical association copied from a small treatment experiment.

Did the investigators chemically measure disulfiram, cocaine, or methadone in blood?

No contemporaneous quantitative forensic venous whole-blood concentration series is reported for those drugs. The actual drug-positive endpoint was urinary benzoylecgonine classification. The study did not supply simultaneously analyzed legal venous whole-blood samples for parent cocaine, cocaethylene, methadone, disulfiram, or specific disulfiram metabolites. It also did not report separately quantified plasma or serum parent-drug concentrations to support a drug-disposition model for the cohort.

Whole blood includes blood cells and fluid. Plasma and serum are separated specimens, and urine is an excreted biological matrix. Concentrations in one are not automatically exchangeable with concentrations in another. A laboratory cutoff in urine cannot be divided by an assumed partition coefficient to create a contemporaneous whole-blood level without validated paired-sample science. Clinical urine positivity also cannot establish an exact time of the last use episode; that would require information and uncertainty analysis beyond this trial’s design.

Could a positive urine result establish impairment, intoxication, or a drug-use clock?

No. The study investigated repeated clinic-screen outcomes for patients in treatment, not drivers at the roadside, workplace fitness cases, witnesses, accidents, or deaths. No standardized field sobriety assessment, on-road driving performance, individualized cocaine dose challenge, or forensic event reconstruction was its principal endpoint. A benzoylecgonine-positive urine collected on a scheduled clinical day may be meaningful for treatment follow-up, but it does not by itself measure brain effects at the hour of a disputed incident.

Also, the intervention was disulfiram—not an experimentally delivered amount of cocaine. A person’s interval from cocaine consumption to collection was not established under a controlled administration sequence. Past-use status, repeated screens, clinical symptoms, and administered treatment are distinct sources of evidence. A defensible forensic opinion must identify which of those were measured and which remain inferential or altogether unmeasured, rather than treat a clinical trial as a validated reverse-time calculator.

Does a 300 ng/mL urinary cutoff establish a chemically confirmed cocaine finding?

The publication identifies the Hitachi automated testing platform and its urine benzoylecgonine decision threshold, but does not present a specimen-by-specimen confirmatory chromatography and mass-spectrometry dossier. The distinction is important. An analyzer’s screening classification is not the same scientific proposition as an independently validated confirmatory identification of cocaine or metabolites with documented retention time, ion ratios, calibrator acceptance, carryover and interference performance, and appropriate chain of custody.

Nor does an outcome label of “cocaine-positive urine” report the exact quantity of parent cocaine. The source names the metabolite benzoylecgonine, and its 300-ng/mL cutoff should remain connected to that urine method. The site has a separately published discussion of confirmatory drug-testing evidence; the procedural distinctions in that guidance should be checked against actual laboratory records when an individual case is at stake.

What do the design limits mean for claims of clinical effectiveness?

This was an exploratory treatment trial with small arms, selective eligibility, common background methadone and behavioral therapy, and notable attrition. It is meaningful that the 250-mg and 375-mg models differed from placebo; that evidence should not be erased simply because other endpoints were nonsignificant. It is equally meaningful that the authors did not detect a significant downward trend within those two medication groups or a significant difference in the exploratory all-starter responder rates. Those results should not be upgraded to an established abstinence-producing therapy.

It would also overstate the evidence to turn a lack of group significance for a vital sign into proof of safety across doses, or to treat the 500-mg arm’s nonsignificant result as a universal contraindication established by this 10-person arm alone. Interpretations of medicinal benefit and harm must reflect the source population and its uncertainty. Clinical treatment choices fall outside this forensic evidence summary and require individualized professional care and current treatment guidance.

How would a careful forensic case review use this paper?

The publication can help explain why repeated qualitative urine drug-testing outcomes in clinical trials must be read together with collection frequencies, missing-data rules, analytical thresholds, and statistical denominators. It is also a concrete example of the difference between a between-group statistically significant slope contrast and an individually tested treatment-group trajectory that does not differ significantly from zero. That analytic distinction can prevent misleading summaries of comparative medical evidence.

For a real case, the source is only contextual scholarship. The reviewer would still need original collection and chain-of-custody records, method validation for the specific matrix and analyte, instrument data, calibrator and QC acceptance, confirmatory results when required, exposure and medication history, relevant examination findings, and precise timing. Evidence about a 49-person treatment cohort cannot substitute for those absent records. The appropriate end point is a carefully bounded explanation of what the study measured and what it did not.

Seven frequently asked forensic questions about the disulfiram trial

1. Did the study prove that 250 mg/day disulfiram stopped cocaine use?

No. The 250-mg arm differed significantly from a placebo group whose positive-urine trajectory increased, but its own negative modeled slope did not differ significantly from zero (p > .15). Positive specimens remained part of the observed treatment course. The experiment does not establish universal abstinence or any particular patient’s response.

2. Was 375 mg/day proven more effective than 250 mg/day?

No. Both selected doses had significantly different slopes relative to placebo, but this is not a reported, adequately powered direct proof that 375 mg was superior to 250 mg. Their independently tested slopes were both nonsignificant relative to horizontal, and the groups each contained only thirteen treated individuals.

3. Did the 500-mg group have no cocaine exposure?

No. Its modeled slope was +0.003, the contrast with placebo was nonsignificant (p > .11), and two of ten week-three starters met the exploratory responder definition. A nearly flat aggregate model coefficient does not describe each person’s exposure or imply urine negativity, much less prove an absence of cocaine use.

4. Does urine benzoylecgonine at 300 ng/mL establish cocaine in blood?

No. The reported 300-ng/mL value is a urine screening cutoff for a cocaine metabolite. Whole blood is a different specimen, and parent cocaine is a different chemical species. The trial provided no validated paired whole-blood cocaine concentrations or inter-matrix conversion equation.

5. Why are 49 patients not 49 multiplied by 39 independent samples?

Forty-nine is the number of actual treated participants. Thirty-nine refers to potential repeated urine-collection opportunities during follow-up, with many missing. Multiple specimens from one person are correlated and cannot be counted as independently enrolled subjects. The source modeled this repeated-measures structure.

6. Did nondifferent heart-rate and blood-pressure group tests establish drug safety?

No. The group-by-week tests reported nonsignificant results for the examined vital signs, but group sizes and eligibility exclusions limit their sensitivity to uncommon harms. The trial also documented adverse-event episodes and individual discharges. Neither a statistical null nor an adverse-event count alone resolves causation in an unrelated person.

7. Could this trial identify when an individual last used cocaine or whether a driver was impaired?

No. It did not administer timed cocaine doses, chemically assay contemporaneous legal venous whole-blood cocaine concentrations, test actual drivers, or construct a validated individual-use-time model. A treatment-program urine-screen trend is not evidence of a precise person’s use clock, driving ability, crash mechanism, or death causation.

Original primary empirical evidence

Oliveto AH, McGaugh J, Chopra MP, Thostenson J, Mancino MJ (2025). A randomized clinical trial of disulfiram at higher doses for the treatment of cocaine use disorder among methadone-stabilized patients. Journal of Psychiatric Research 186:387–395. Read the original primary study: DOI 10.1016/j.jpsychires.2025.04.051. Its clinical observations support the narrowly defined comparisons above; any application to a particular laboratory report or legal matter requires independently verified case-specific evidence.