Does Methamphetamine Cue-Avoidance Training Prevent Relapse? A 24-Patient Pilot Found No Significant Benefit and Important Safety Concerns

Short answer: In a 2026 randomized pilot involving 24 people receiving residential treatment for methamphetamine use disorder, a personalized computer-based approach-bias modification program produced numerically higher self-reported abstinence percentages than sham training. But none of the reported abstinence comparisons established a statistically significant treatment benefit. Eight of 24 participants reported distress or craving reactions associated with training, and three withdrew because of distress. The study therefore raises a clinically relevant safety question without establishing either effectiveness or ineffectiveness in a sufficiently powered trial. It did not administer methamphetamine, measure post-training methamphetamine in forensic whole blood, or prove that a particular person’s use, craving, testimony, or future relapse could be identified from computer-task performance.

The primary research is Victoria Manning and colleagues, Approach With Caution: A Pilot Randomised Controlled Trial of Approach Bias Modification for People Undergoing Residential Treatment for Methamphetamine Use Disorder, Drug and Alcohol Review (2026), DOI 10.1111/dar.70151. The original authors compared personalized avoidance training with a task designed to resemble it without consistently pairing methamphetamine images with avoidance movements. What matters is the distinction between a suggestive difference in a small sample, a demonstrated causal benefit, a report of adverse reactions, and a measured toxicological result.

What question did the randomized trial actually ask?

Its main practical question was whether repeatedly pushing away individually salient methamphetamine-related images, while pulling personally meaningful positive images toward oneself, might improve abstinence after discharge from residential treatment. The investigators also examined treatment acceptability, craving, dependence severity, the timing of illicit stimulant use after discharge, and adverse psychological reactions during training. These are legitimate clinical outcomes, but they are not equivalent: an immediate task-related craving episode, a retrospective report of past-month drug use, and a clinical dependence interview each interrogate different phenomena.

Crucially, this was a pilot rather than a definitive efficacy experiment. Recruitment was intended to be much larger, but pandemic restrictions, loss of a recruiting site, eligibility barriers, and the end of funding left only 24 randomized participants. Small samples can provide useful feasibility and safety signals, yet a difference that happens to favor one arm cannot be treated as proof that the intervention prevents relapse. Conversely, a nonsignificant trial cannot establish that the treatment would never work under different circumstances.

Who entered the study, and what is the correct independent sample size?

Twenty-four adults with recent moderate or severe methamphetamine use disorder were randomized across four residential services in metropolitan Melbourne, Australia, during 2020–2024. Ten were assigned to personalized approach-bias modification (ApBM) and fourteen to sham training. The participants’ average age was 31.82 years, and fifteen were men. Although the underlying computer exercises generated hundreds of responses per session, the independent experimental sample remained 24 people, not thousands of image trials or the sum of repeat follow-up interviews.

Selection matters. Eligibility required recent methamphetamine use and a stated intention to remain in treatment long enough to complete six sessions. Clinicians were asked not to refer people unable to consent or participate safely. The results therefore do not describe everyone seeking emergency care after acute intoxication, people outside residential treatment, or a random sample of drivers. Eighteen of twenty-four reported a non-substance psychiatric diagnosis, and additional drug concerns were common; the intervention was embedded in heterogeneous residential programs rather than delivered as an isolated medication-like exposure.

The randomized arms were also visibly different at baseline. Mean age was 27.09 years in the training group and 35.20 in sham. Reported methamphetamine consumption over the four weeks before admission averaged 23.40 grams versus 12.44 grams, respectively. Mean residential admission lasted 40.88 days versus 28.15 days among participants with duration data. Those descriptive imbalances are not proof of bias, but with ten and fourteen allocated people they could materially affect the interpretation of later outcomes and could not be reliably disentangled by extensive covariate adjustment.

How was personalized approach-bias modification delivered?

The active arm began by evaluating forty methamphetamine-related and forty positive images. Investigators used each participant’s ten highest-rated images from each category. Drug-related scenes could reflect personally familiar drug-use contexts, while positive scenes could represent valued goals such as family, activity, work, or recreation. Across six planned sessions over approximately two weeks, each twenty-image personalized set was repeated twelve times per session, producing 240 image trials per session. Those trials were repetitions nested within the same patient.

Participants moved a joystick according to the frame orientation of each picture. Ninety-five percent of landscape-framed images in the active task were methamphetamine related and thus tended to be pushed away; ninety-five percent of portrait-framed images were positive and thus tended to be pulled toward the viewer. This created the intended repeated avoidance versus approach association. The controls also moved a joystick and saw methamphetamine and positive images, but the two image types were divided equally across approach and avoidance movements. The control used the full forty images of each type, generally three times each, yielding a comparable number of task presentations without a systematic bias-training contingency.

This design is importantly different from administering a psychoactive drug. The study imposed repeated visual and motor contingencies; it did not provide an acute dose of methamphetamine, collect a post-dose concentration curve, or test whether patients could later identify a forensic drug specimen. The intervention may alter attention or affect, but only outcomes actually measured and adequately analyzed can establish those effects.

What were the principal group sizes, denominators, and safety observations?

These figures have different denominators and collection mechanisms. The proportion experiencing a training-related psychological reaction is based on the 24 randomized people. The abstinence fractions are among those whose status was ascertained at the specified follow-up, often by telephone and retrospective self-report. A seemingly favorable percentage must never be detached from how many people were actually observed.

Did training significantly increase one-month abstinence?

No statistically significant difference was demonstrated. At the one-month assessment, five of seven assessable ApBM participants reported no illicit amphetamine use in the relevant period, compared with five of eleven controls: approximately 71% versus 45%. Fisher’s exact comparison yielded p = 0.367. This is a numerical direction favoring training, but it does not meet the customary .05 threshold and does not provide a reliable estimate of a personalized patient’s future abstinence probability.

The investigators also showed the effect of treating every randomized person lost to follow-up as non-abstinent: five of ten active versus five of fourteen controls, or 50% versus about 36%, with p = 0.678. This conservative missing-as-use scenario is a sensitivity assumption, not evidence that every missing person relapsed. It illustrates how the headline percentage changes when the denominator changes. One additional active-arm patient’s early abstinence status was collected retrospectively at the later interview, another reminder that ascertainment time and report time are not always the same.

What happened at the three-month follow-up?

Past-month abstinence was reported by four of seven assessable active participants and three of nine controls, approximately 57% versus 33%; the actual Fisher comparison was p = 0.615. Applying the investigators’ conservative missing-as-use assumption to all randomized participants yielded 40% in the active arm and about 21% in controls, with p = 0.393. Neither version demonstrated a statistically significant intervention benefit. The denominator cannot be swapped mid-analysis without explicitly explaining what changed.

A stricter question was continuous abstinence since discharge through the three-month assessment. Three of seven assessed ApBM participants and two of eleven controls reported that outcome: approximately 43% versus 18%, with p = 0.326. On the original randomized denominators the comparison was three of ten versus two of fourteen, with p = 0.615. Continuous abstinence is not interchangeable with abstinence during only the preceding twenty-eight days. A person can report no recent use at three months without having been continuously abstinent since leaving treatment.

Was time to first illicit stimulant use delayed?

The Kaplan–Meier analysis estimated a median time to the first reported lapse of 35 days in the personalized-training group and 14 days in the sham group. The published 95% confidence intervals were broad: 19–50 days and 0–55 days, respectively. The between-group log-rank comparison was χ²(1) = 1.43, p = 0.232, meaning that the observed survival curves did not establish a statistically significant difference. The visible separation in a plotted curve must be interpreted together with uncertainty, censoring, and the small number of people at risk.

For this analysis, the authors counted any non-prescribed amphetamine-type stimulant use as a lapse. That definition is broader than a validated laboratory confirmation of methamphetamine on a particular date. It may be suitable for a clinical relapse inquiry, but not for reconstructing an unknown person’s dose, route, blood concentration, time of last use, or criminal responsibility. In a forensic case, those questions require a separate chain of evidence.

Which measured clinical outcomes remained nonsignificant?

The numerical findings in this table are taken from the authors’ results, but they do not exhaust all tests conducted. At one month, reported days of use, grams used, craving strength, and dependence severity did not significantly distinguish groups. At three months, reported days of use, grams used, craving frequency, and dependence severity were also nonsignificant. It would be misleading to transform these null comparisons into positive confirmation that the mechanism worked merely because some observed percentages moved in the desired direction.

Did personalized cue avoidance reduce craving?

The published follow-up craving questionnaire did not show a significant difference between randomized arms. At one month, craving-frequency scores averaged 2.25 (SD 2.52) after active training and 2.06 (SD 2.04) after sham, p = 0.871. Three-month craving-strength means were 3.43 and 3.44, p = 0.992. These particular questionnaire values concern experiences reported during a recent period, not continuous objective physiological recordings and not an assay for methamphetamine. They also do not mean participants never experienced a powerful reaction when images appeared.

The separate pre-session and post-session visual analog craving item was collected to monitor immediate safety. Some participants described exposure to their cue photographs as upsetting or triggering. A mean follow-up score that fails to differ significantly cannot negate a documented adverse experience in an individual participant. Conversely, an immediate craving increase during an intervention is not proof that the participant used methamphetamine afterward; the study must be read at the proper observational level.

What was the safety signal—and did it occur only with active training?

It occurred in both groups. Three participants assigned to personalized training and five assigned to sham experienced a reported negative psychological reaction to the task, including distress or craving triggered by its content. Three participants withdrew because of that distress: two in the active arm after one session each and one sham participant after two sessions. A participant in the active group required immediate psychological support and quetiapine, while another participant in the sham arm received diazepam after a session. These reported clinical responses warrant attention without presuming a medication was required for everyone or that the training caused a diagnosable psychiatric illness.

The three withdrawals arose at the same recruiting site, which then ceased participation in the trial. Other participants experienced distress but continued training. In a trial with only 24 randomized people, an eight-person adverse-reaction count is clinically salient even without a precise between-arm risk estimate. It establishes that the chosen intervention and control procedures were not uniformly experienced as benign. The sham task still exposed patients repeatedly to personally relevant drug imagery and active joystick responses, so “sham” should not be translated into “no psychological exposure.”

Neither randomization nor a positive acceptability score overrides those observed events. Safety findings concern what happened during this pilot, while comparative safety and a causal adverse-event rate would require larger samples, standardized ascertainment, and possibly different comparator tasks. Patients in recovery may experience drug cues differently; the data do not justify assuming that a person with a particular legal history will respond the same way.

Why did acceptability ratings look favorable despite withdrawals?

Participants who completed all six sessions generally rated the program acceptable. The Endorsement and Discomfort Scale means were 69.13 in the active group and 58.83 under sham; the between-group result was p = 0.139. Yet these scores came from survivors of the full training course rather than everybody originally randomized. Someone who withdrew because images were triggering was less likely to contribute a favorable final acceptability score. This is a classic source of selection bias when a completion-dependent outcome is summarized as though it represented everyone offered the intervention.

Blinding was imperfectly reassuring. Among respondents asked to guess their allocation, six of seven in the active arm and six of eleven controls believed they received the active training, p = 0.316. This nonsignificant comparison does not demonstrate that participants were unaware of their condition, particularly where task personalization and orientation frequencies differed. Investigators administering training could see which task was shown, although follow-up interviews were conducted by a separate blinded researcher.

What did the study actually measure about methamphetamine?

It documented histories of methamphetamine and other illicit amphetamine-type stimulant use, using a structured clinical interview, severity scales, retrospective timeline follow-back reports, and craving ratings. It did not administer a controlled methamphetamine dose to participants, quantify post-intervention parent methamphetamine in venous whole blood, measure a validated plasma or serum concentration–response curve, or use laboratory-confirmed serial urine specimens as its primary abstinence endpoint. Grams reportedly consumed before admission are historical self-reports, not body-burden measurements.

That distinction matters because different questions require different evidence. A validated analytical method could identify methamphetamine or metabolites in a collected specimen, with results constrained by the actual matrix and testing window. A clinical report of no use during the previous month asks about behavior across time; it cannot be rewritten as a measured blood drug concentration of zero. Likewise, a positive urine screening result in another setting would not by itself establish intoxication at an alleged event. The practical differences between specimens are explained in the site’s biological matrices guide, while the specificity and limits of chemical findings are addressed in its confirmatory drug testing guide.

Can a computer task establish an individual’s relapse risk or credibility?

No validated person-level diagnostic performance was established. A clinical team might reasonably consider cue-triggered craving in choosing and monitoring care, but the published pilot does not supply sensitivity, specificity, positive predictive value, validated individual thresholds, or an externally tested predictive rule. It does not show that one observed joystick response or image-avoidance score correctly identifies a person who is using methamphetamine or will relapse. The research concerns randomized group-level estimates and adverse responses, not a courtroom test for honesty or future conduct.

Clinical concern about craving also differs from proof of intent. The investigators did not measure witness veracity, criminal state of mind, road behavior, or the causal role of drug exposure in an injury. A witness who reports craving, abstinence, or avoidance cannot be judged scientifically truthful or untruthful merely because another small treatment cohort showed certain group means. The appropriate forensic question is what the actual patient or case record measured, how it was verified, and how much inferential distance separates that evidence from the proposed conclusion.

What statistical and design limitations most affect interpretation?

The trial randomized twenty-four people against an intended recruitment target of roughly one hundred, and no conventional prospective power calculation had fixed the final sample size. Small groups naturally produce wide uncertainty around differences in relapse proportions. Follow-up denominators varied by outcome and time point, so reported 71%, 57%, or 43% percentages cannot simply be treated as observed outcomes for all ten active participants. The authors supplied conservative missing-as-use analyses, which also failed to establish significant benefit.

Baseline imbalance, varying durations of residential treatment, program differences between sites, concurrent psychiatric conditions and other drug concerns, and the COVID-era recruitment setting all complicate attribution. The mean residential stay differed by approximately thirteen days between arms in available data. With so few participants, adjustment for many prognostic factors was impractical. The sample was drawn from metropolitan Melbourne and consisted of volunteers within treatment—not a representative sample of all people who use methamphetamine.

The investigators’ outcomes were numerous: several versions of abstinence, days and grams used, craving frequency and intensity, dependence severity, acceptability, time to lapse, and adverse events. A result that is descriptive rather than inferential should not be promoted to confirmatory status, while a genuine reported p value should not be inflated into diagnostic accuracy. The pilot is best understood as a feasibility-and-safety inquiry that can inform hypotheses and safeguards for a future study, not a definitive treatment prescription.

What evidence would a stronger next trial need?

A larger adequately powered randomized study would need prespecified primary outcomes, consistent definitions of methamphetamine versus other illicit stimulant use, well-characterized follow-up losses, transparent comparator effects, and longer observation. Independently corroborated self-reports where feasible might strengthen the abstinence endpoint; any collected urine, oral-fluid, plasma, or whole-blood results would need validated analyte-specific methods and clearly identified matrices. Chemical confirmation would not automatically establish craving or impairment, but it would answer a different question from self-report.

Future intervention protocols should also prespecify monitoring and response to psychological distress, including the timing and intensity of personally salient images, criteria for pausing treatment, access to immediate clinical support, and transparent reporting of withdrawals in both study arms. The original authors discussed delaying this sort of training until a later phase of recovery as a possible safety strategy. That suggestion was not itself experimentally shown to prevent adverse reactions in the present pilot; it is a proposal for further investigation.

Importantly, determining clinical usefulness requires balancing any reproducible abstinence benefit against the frequency and severity of cue-triggered distress. Neither side of that balance was settled by twenty-four participants. A detailed future evidence review should examine whether improved task performance transfers to drug-free days after residential treatment and whether results persist outside the specific image stimuli practiced in training.

How should forensic and clinical readers use these findings?

First, keep the denominator attached to every result: ten versus fourteen were randomized, but the assessable abstinence samples were smaller. Second, distinguish the apparent direction of change from statistical support: the relapse comparisons were not significant. Third, treat training-associated distress as a real documented observation while resisting a false comparative risk estimate from tiny cells. Fourth, do not interpret craving questionnaires, joystick movements, reported past-month drug use, and laboratory drug concentrations as interchangeable measurements.

In litigation or evaluation, an expert should ask whether the specific person’s timeline, clinical status, treatment records, independently verified chemical tests, and relevant contextual evidence actually support the claimed inference. This paper cannot retrospectively determine an individual’s methamphetamine concentration at an event, the accuracy of a witness’s memory, or whether an alleged action was caused by a drug. The site’s therapeutic monitoring guide provides additional context for why timed chemical measurements—when they exist—answer different questions from behavioral observations. In the absence of specimen-based measurements here, the study’s strongest conclusions remain clinical feasibility, uncertain efficacy, and a safety signal deserving further examination.

Frequently asked scientific questions

1. Did personalized methamphetamine approach-bias modification significantly prevent relapse?

No. The pilot’s observed abstinence percentages favored personalized training, but the reported one-month, three-month, continuous-abstinence, and time-to-first-use comparisons were nonsignificant. A larger trial is needed before claiming efficacy, and this pilot also cannot conclusively exclude a possible effect.

2. How many patients actually entered the randomized trial?

Twenty-four different patients were randomized: ten to personalized training and fourteen to sham. Repeated photographs, computer trials, and follow-up interviews do not increase the independent participant count.

3. Were eight adverse reactions limited to the active training group?

No. Three active-arm and five sham-arm participants experienced reported distress or craving reactions. Three people withdrew due to distress: two active and one sham. Both tasks involved exposure to methamphetamine-related images.

4. Were the favorable abstinence percentages based on all randomized patients?

No. For instance, one-month reported abstinence was 5/7 versus 5/11 among those with ascertained status. A conservative analysis counting missing participants as non-abstinent changed the denominators to 5/10 versus 5/14; it remained nonsignificant.

5. Did the researchers chemically quantify methamphetamine in venous blood?

No. This was not a measured whole-blood or separated-plasma methamphetamine pharmacokinetic trial. Its relapse outcomes principally reflected clinical interviews and retrospective reports rather than a validated continuous chemical exposure series.

6. Did reported craving scores demonstrate a treatment effect?

No. The follow-up craving measures shown in the original numerical tables did not differ significantly between groups. Immediate cue-triggered distress nevertheless occurred in some participants and is a separate safety observation.

7. Could this study show whether a particular driver or witness was impaired, truthful, or about to relapse?

No. There was no prospective validated individual classifier, chemical intoxication threshold, real driving assessment, credibility measure, or incident-specific causation study. Clinical group observations cannot be substituted for case-specific forensic evidence.

Primary research and scope of interpretation

This analysis is based on Manning V, Whelan D, Piercy H, Hopwood M, Maloney M, Kotler E, Okedara G, Lubman DI, Arunogiri S, Garfield JBB. Approach With Caution: A Pilot Randomised Controlled Trial of Approach Bias Modification for People Undergoing Residential Treatment for Methamphetamine Use Disorder. Drug and Alcohol Review (2026), 45:e70151. Read the original primary scientific paper, DOI 10.1111/dar.70151. Its randomized group comparisons, denominators, outcome definitions, and limitations—not an extrapolation about any individual case—control the interpretation.