Can Smartphone Working-Memory Training Improve Self-Control During Methamphetamine Treatment? A 35-Patient Pilot

Short answer: A small 2017 pilot in a South African residential program found favorable changes in several self-reported mood, self-control, impulsivity, and self-regulation scores among 20 participants who added four weeks of smartphone working-memory exercises to usual care, compared with 15 participants receiving usual care alone. But the primary repeated-measures analysis did not detect a significant treatment-group-by-time interaction across the main outcomes, and several specific between-group tests were also nonsignificant. The experiment did not measure post-training methamphetamine relapse, individual driving ability, or quantitative methamphetamine concentrations in forensic blood. It supports a preliminary question about training and reported psychological functioning, not proof that an individual recovered cognitive control or was free from impairment.

The sole empirical source is Brooks, Wiemerslage, Burch, Maiorana, Cocolas, Schiöth, Kamaloodien, and Stein (2017), The impact of cognitive training in substance use disorder: the effect of working memory training on impulse control in methamphetamine users, Psychopharmacology 234:1911–1921, DOI: 10.1007/s00213-017-4597-6. The interpretation below stays with that original study’s participants, instruments, comparisons, and missing endpoints.

What did the original research actually ask?

The investigators wanted to know whether an inexpensive, adaptive, smartphone-delivered working-memory task could be added to an existing inpatient treatment program for methamphetamine use disorder, and whether participants’ questionnaire responses would change during that period. The proposition was mechanistic in a broad psychological sense: practice maintaining and updating information might help a person pause, plan, and regulate responses. The study was not an analytical toxicology experiment designed to identify methamphetamine molecules, nor was it a test of a person’s response to an administered stimulant dose.

Its central question has two parts that are easy to confuse. One is whether people become better at the very working-memory exercise they practice. The other is whether that practice transfers to daily-life self-control, fewer impulsive decisions, improved clinical recovery, or reduced drug use. A training curve speaks most directly to the first. Questionnaires speak indirectly to the second. Actual drug use, confirmed abstinence over time, occupational performance, and legal impairment would require further, different evidence.

Who participated, and what was the true sample size?

The original recruitment flow began with 90 people screened for eligibility and described an initial group of 25 healthy controls and 41 patients with methamphetamine use disorder who completed baseline assessments. The final treatment comparison included 35 independent patients: 20 who completed additional cognitive training and 15 who completed treatment as usual. Six of the 41 baseline patients did not complete the follow-up, four from the training pathway and two from usual care. These denominators are important because outcome means reported at baseline and follow-up do not always describe the same number of people.

The healthy comparison group contributed baseline information, not an additional randomized course of smartphone training. The original article’s Table 2 uses 21 healthy controls for several completed psychological-scale analyses, although Table 1 and the participant flow diagram describe 25 controls. For that reason, one must not casually claim that 25 control participants provided complete data for every questionnaire. The treated clinical cohort also has different baseline and follow-up denominators in Table 2: 24 training and 17 usual-care baseline entries, compared with 20 and 15 follow-up entries.

Participants were drawn from a Cape Town inpatient rehabilitation service and had a reported history of methamphetamine use. According to the investigators, patients had been abstinent for at least two weeks at the point of assignment. Their prior exposure history was measured in years, not from quantitative postdose specimen sampling. The researchers did not enroll a representative cross-section of drivers, patients with acute poisoning, or people undergoing criminal forensic examinations.

How were participants allocated, and was this a definitive clinical trial?

After baseline assessment, patients received either the existing residential program alone or that program plus smartphone practice. The article uses random-allocation language, while its recruitment flow also describes alternating first-come-first allocation. The original authors expressly characterize the work as a pilot exploratory study of self-report measures, not clinical outcomes. Those details matter more than an attractive shorthand such as “randomized proof of efficacy.” Allocation procedures, group comparability, sample attrition, and the nature of the endpoints all affect the strength of causal conclusions.

The participants and staff could necessarily distinguish doing daily extra exercises from not doing them. Expectation, attention from staff, enthusiasm about a novel device, and ordinary improvement during several weeks of inpatient rehabilitation could therefore contribute to outcomes. The baseline groups were not large enough to ensure balance in every clinically relevant factor. An exploratory pilot can generate useful hypotheses without conclusively separating the specific effect of n-back practice from broader treatment and context.

What did treatment as usual involve?

The background residential program was substantial. During an eight-week course, the service provided a structured living environment with daily dialectical behavior therapy on weekdays for approximately six weeks, alongside psychoeducation, social and practical skills activities, and physical activity. The investigators assessed their adjunct during a four-week window after an initial induction period. Thus the comparison was usual care plus training versus usual care, not smartphone training against an absence of treatment.

This structure limits interpretation in two directions. Favorable changes in both groups may reflect the established treatment program or the passage of time. Differences between groups may be associated with the extra exercises, but potentially also with additional engagement and expectancy. There was no pharmacological treatment arm that administered methamphetamine, dextroamphetamine, methylphenidate, or another psychostimulant to test a concentration–effect relationship. The drug identified in the diagnosis and history was not a newly measured exposure in the experimental protocol.

What happened during four weeks of smartphone training?

The added intervention used an adaptive n-back task. Participants viewed a sequence of letters and responded when the current item matched a specified previous position in the sequence. At the easiest levels the comparison involved the current or immediately preceding item; at harder levels it required maintaining and updating information over more intervening letters. Commission errors meant responding to a nontarget; omission errors meant missing a target. The researchers scored task accuracy from these responses, rather than from a biological drug assay.

Training was scheduled for roughly thirty minutes per weekday across four weeks, or up to twenty sessions. Advancement to the next difficulty level required achieving approximately 80% accuracy on the preceding level. This was intended to keep the task challenging rather than allowing participants to remain indefinitely at a level they had mastered. A session count is not an independent participant count: one person can generate many letter presentations, many errors, many accuracy values, and repeated performance observations without adding another person to the sample.

Did people actually learn the task they practiced?

The researchers fitted a learning curve to accuracy over consecutive days at the hardest three-back level and reported R² = 0.3523 with p < 0.05. They referred to this result as a 35% learning rate. In precise statistical terms, the R² value indicates the proportion of observed variation explained by the fitted training trend; it is not evidence that a person’s overall memory capacity, self-control, or public-safety performance improved by 35 percentage points.

Only 12 of the 20 training completers consistently practiced at the three-back level and entered the specific plotted learning-rate analysis. Eight others moved intermittently between the two-back and three-back difficulty levels. Looking only at the 12 more consistently advanced users reduces the direct generalizability of that training curve even to the full training arm. A rising performance trajectory on a practiced computerized exercise is important feasibility evidence, but a separate untrained neuropsychological assessment would better measure broader transfer.

Which questionnaires and task measures were collected?

The investigators used visual analogue scales to rate current mood, desire for the drug, and feelings of self-control. They also used the Hospital Anxiety and Depression Scale (HADS), the Barratt Impulsivity Scale (BIS), and a Self-Regulation Questionnaire (SRQ). Trail Making was included as an executive-function task, using the difference between the time to complete parts B and A. Those measures are not interchangeable: a mood rating is not a drug concentration, and a self-described improvement in planning is not the same thing as an objectively observed decision in traffic.

The instruments can nevertheless be useful within their intended research setting. Asking about current perceptions can reveal what patients report while undergoing rehabilitation. Higher perceived control may have clinical relevance if it persists and predicts improved choices. But the study did not simultaneously test whether the rating changes caused independently verified changes in methamphetamine use. Questionnaire scores also can shift with situational reassurance, desire to please an assessor, attention from staff, or willingness to endorse certain descriptions.

What were the principal observed group means?

Table 2 of the original paper supplies useful descriptive figures. They are means with standard deviations, not results of chemical testing and not a guarantee that any particular person experienced the same change. The baseline columns contain 24 training and 17 usual-care patients; the follow-up columns contain 20 and 15. The table below deliberately presents group means rather than constructing an unjustified paired difference from samples with unequal follow-up coverage.

The descriptive pattern is favorable for several training-arm self-reports, particularly mood and perceived control, but different baseline and follow-up sample sizes prevent assuming complete within-person change for everybody shown. The contrast also depends on the underlying statistical analysis, not on whether one group’s last column simply looks numerically larger. The smaller usual-care group provides a noisy comparison, and the pilot was not designed to estimate a precise effect for the larger treatment population.

Which results were statistically significant and which were not?

The distinction between descriptive differences and inferential results is crucial. The authors’ repeated-measures multivariate test for the treatment group × time interaction was not significant (F = 1.038, p = 0.382). The source also reports significant main effects in some pooled measures. These omnibus results counsel against declaring that the training intervention established a consistent, across-the-board improvement relative to usual care.

The original printed Table 3 gives several exploratory pairwise tests. Some numbers there differ from corresponding narrative sentences elsewhere in the publication, so the following table explicitly uses the printed Table 3 between-group follow-up column without silently combining discordant p-values. A p-value near a conventional threshold does not provide a clinically validated response criterion, especially when many exploratory outcomes and subscales were compared.

The original narrative additionally describes within-training-group improvements in perceived control, planning-related impulsivity, mood and some self-regulation subscales. Those results should not be mistaken for definitive treatment-by-time interaction evidence. Conversely, nonsignificant comparison tests do not prove two treatment approaches are equivalent. The small sample and attrition leave substantial uncertainty. The source reports Bonferroni adjustment in parts of the multivariate procedure while labeling other subscale analyses exploratory; a reader should not assume every individual p-value above represents a fully prespecified familywise-controlled result.

Was desire for methamphetamine demonstrably reduced by training?

The training group’s mean desire-for-drug visual-analogue score fell descriptively from 20 to 14, and the usual-care group’s mean from 20 to 17. In the source’s printed between-group follow-up comparison, however, the difference in desire-for-drug rating was not statistically significant (p = 0.371). The proper conclusion is therefore not that a smartphone n-back exercise reliably suppressed craving relative to ordinary residential treatment. An apparent shift in an average can occur without a convincing between-group intervention contrast.

It is also important to distinguish an immediate self-report of wanting a drug from later biologically verified use. A person may report less current desire while still struggling with environmental triggers after leaving a structured facility. The trial did not prospectively validate a personalized relapse cutoff based on VAS response, nor did it show that the change in perceived desire was accompanied by a different confirmed toxicology trajectory. The source’s prospective treatment implications are appropriately hypotheses for future clinical work, not forensic facts about a particular person’s future conduct.

Did cognitive training show objective gains beyond the practiced task?

The fitted three-back performance curve supports improvement on the specifically practiced working-memory task for the 12 consistent higher-level trainees. But broader transfer is harder to establish here. Trail Making B-minus-A was included as a separate executive-function measure; its between-group follow-up result in the printed Table 3 was not significant (p = 0.439). The article describes a within-usual-care improvement in that task, not a clear preferential benefit from adding cognitive training.

No independent laboratory stop-signal measure, on-road driving examination, case-specific hazard-recognition test, or postdischarge occupational performance endpoint was validated as an outcome of this pilot. A reduction in total BIS self-rated impulsivity within the training group has a different evidentiary status from an observed reduction in actual impulsive actions. Clinical relevance requires asking whether apparent gains persist, generalize to unfamiliar tasks, and survive a credible control for repeated testing and treatment expectations.

What about baseline differences and attrition?

At baseline the methamphetamine-use group generally reported less perceived self-control, more depressive symptoms, greater impulsivity and lower self-regulation than the healthy comparison group. Those observations are consistent with difficulties experienced by this selected population, but they cannot establish that historical drug exposure was the exclusive biological cause. Pre-existing vulnerability, educational opportunity, stress, comorbid conditions, rehabilitation selection and many other variables can contribute. This was not a longitudinal controlled exposure study beginning before drug use.

Six clinical participants left before follow-up from the 41 baseline methamphetamine-use group. That reduction is consequential in a study whose final training comparison involves only 20 versus 15 people. If those who left differed systematically in willingness, symptoms, or task performance, the complete-case pattern may not generalize even to the full baseline group. The authors also noted that only 12 consistently achieved the hardest practice level. The reported task learning and subjective follow-up changes therefore rest on different subgroups and cannot be treated as one uniform effect measured in an identical N.

Were whole blood, plasma, serum, or methamphetamine metabolites assayed?

No quantitative methamphetamine concentration endpoint was reported in this original intervention study. The relevant specimen distinction is not semantic. Forensic venous whole blood includes cells and plasma together; plasma is the separated liquid phase; serum is collected after coagulation. Urine, oral fluid, hair, sweat and tissue have different biological and interpretive properties. An outcome in one material cannot be substituted with a questionnaire result or assumed from a subject’s recorded diagnosis.

The study involved patients with a history of methamphetamine use; the additional intervention was a computerized cognitive task, not an administered pharmacological challenge. The authors described clinical abstinence screening and supervision within rehabilitation, but did not publish concentrations, analyte identities from confirmatory chromatograms, calibration ranges, whole-blood collection times, matrix-specific detection limits or a participant-level pharmacokinetic series. Accordingly, the apparent behavioral response cannot be converted into an estimated methamphetamine blood level, route of use, last-use time or biological clearance interval.

For additional specimen context, see the existing guides on biological matrices and confirmatory drug testing. These are general scientific frameworks, not missing analyses supplied retrospectively to the Brooks experiment.

Can the result establish sobriety, impairment, or future relapse for one person?

No. A psychological-scale mean is a distributional descriptor, not a diagnostic rule. A higher self-control rating could coexist with a positive drug screen, and a lower rating could occur in a person without any contemporaneous drug exposure. The experiment did not evaluate validated sensitivity or specificity for an individual impairment classifier, derive a blood concentration cutoff, or compare a person’s results with observed driving under controlled conditions. It did not determine whether a named patient was truthful, able to operate machinery, or responsible for a particular collision.

Nor did it establish a verified long-term relapse reduction after discharge. Relapse is a temporally extended clinical outcome requiring an operational definition, follow-up coverage, and appropriate biological or independently corroborated assessment. Self-regulation measured during a supervised program is relevant as a proposed intermediate mechanism, but is not a replacement for that outcome. The original authors themselves described the study’s focus as psychological self-report rather than formal clinical treatment endpoints.

How should an attorney or forensic toxicologist use this study?

First identify the offered proposition. If the claim is that a brief smartphone exercise can be implemented in a residential setting and is associated with certain favorable questionnaire changes in a small pilot, the study provides preliminary evidence. If the claim is that working-memory training reliably prevents methamphetamine relapse, restores objective neurocognitive capacity in all patients, establishes verified abstinence, or negates impaired-driving evidence in a particular case, the study does not test the necessary endpoints.

A disciplined expert comparison asks for the number of independent patients; which outcomes were objective versus self-report; whether the relevant p-value came from an overall interaction, a pairwise test, or a within-group contrast; how many tests were run; which people completed follow-up; and whether a biological specimen was collected and chemically analyzed. Source-table and prose discrepancies also deserve reconciliation against the original pages rather than importing a convenient number from a secondary summary. Clinical progress deserves recognition without being transformed into unsupported legal conclusions.

Where a case contains genuine laboratory evidence, examine the specimen, analytical method, chain of custody, calibration, controls, identity criteria and timing separately. Guidance on therapeutic drug monitoring can illustrate why a pharmacological concentration question differs from a behavioral treatment question, though that clinical subject did not form a measured endpoint in this trial.

Frequently asked scientific and forensic questions

1. How many people contributed to the treatment comparison?

Thirty-five distinct methamphetamine-use-disorder patients completed the final comparison: twenty received usual care plus four weeks of smartphone training and fifteen received usual care alone. Forty-one had baseline clinical assessments, and the healthy-control recruitment group was separate. Counts of practice sessions, letters, or questionnaire items are repeated observations rather than additional independent patients.

2. Does the reported 35% learning rate mean that memory or self-control improved by 35%?

No. The reported number is R² = 0.3523 for a fitted progression in the practiced three-back exercise among twelve consistently advanced trainees. It is not a validated percentage increase in general cognition, driving skill, or abstinence probability. The other eight training completers did not consistently stay at that level.

3. Was training better than usual care for every outcome?

No. Several questionnaire comparisons favored the training group, but the overall group-by-time multivariate result was not significant (p = 0.382). Between-group follow-up differences for desire-for-drug, Trail Making and total Barratt impulsivity were also nonsignificant in the printed Table 3. The paper warrants a selective, exploratory interpretation rather than a blanket efficacy claim.

4. Were methamphetamine concentrations measured in participants’ blood?

No quantitative forensic whole-blood or separated plasma or serum methamphetamine concentrations were reported as intervention outcomes. The experimental exposure was cognitive practice within rehabilitation, not a controlled drug dose. There is no concentration–effect curve from which to deduce a patient’s drug level, exact use time or impairment.

5. Does a lower desire-for-drug rating prove future abstinence?

No. A same-day rating is not a prospective validated relapse outcome. The relevant training-versus-usual-care follow-up comparison for desire was nonsignificant in the printed Table 3 (p = 0.371), and the study did not establish a sustained, biologically verified postdischarge relapse advantage.

6. Did the pilot prove a transferable objective improvement in inhibition?

Not conclusively. Practiced n-back accuracy and subjective impulsivity scales were studied, while objective Trail Making did not show a significant between-group follow-up difference. The paper did not report a validated external driving, stop-signal, crash-risk, or courtroom-specific cognitive competency endpoint. Transfer to those tasks remains an open research question.

7. Can this evidence determine an individual person’s intoxication or legal responsibility?

No. Historical methamphetamine diagnosis, n-back performance and self-ratings cannot replace case-specific toxicology, clinical examination, witnessed behavior, validated impairment assessment or reconstruction of an incident. The study cannot independently tell whether a particular person was drug-positive, fit to drive, impaired, abstinent, or responsible for a specific event.

Bottom line: a promising rehabilitation hypothesis, not a blood-drug or impairment test

Brooks and colleagues demonstrated the practical delivery of an adaptive four-week working-memory exercise alongside residential care, with favorable reports for selected mood and control measures among the training completers. Equally important are the nonsignificant overall interaction, several nonsignificant exploratory between-group contrasts, differential numbers at baseline and follow-up, selection of only twelve consistent three-back performers for a learning curve, and absence of quantitative drug sampling or longer-term verified relapse assessment.

Forensic interpretation should preserve both sides of the evidence. It is reasonable to say the pilot generated support for further controlled work on cognitive-training adjuncts in methamphetamine treatment. It is not reasonable to infer a specific person’s forensic whole-blood concentration, time of last use, legally relevant impairment, driving capability, or causation from that pilot’s questionnaire scores. The original empirical reference is Brooks SJ, Wiemerslage L, Burch KH, Maiorana SA, Cocolas E, Schiöth HB, Kamaloodien K, Stein DJ, Psychopharmacology (2017) 234:1911–1921: https://doi.org/10.1007/s00213-017-4597-6.