Author: toxlaw

Vitreous ethanol is not invariably higher than blood ethanol. In 31 forensic cases, Savini and colleagues reported higher vitreous concentrations in 23 cases and higher blood concentrations in eight. The findings support examining vitreous alongside blood, while showing why a presumed fixed relationship can misdescribe an individual case.

Which specimens were compared?

The study examined 31 cases of suspected ethanol poisoning at the Hospital “Santo Spirito” laboratory in Pescara, Italy, during 2019. These were selected forensic cases, not a random sample of deaths or a controlled drinking experiment.

Blood was collected before opening the body, mainly from the femoral vein. “Mainly” matters: the report does not establish that every specimen came from the same vessel. Vitreous was obtained from both eyes by needle puncture. All specimens received sodium fluoride at 100 mg per 10 mL of sample, were stored at 4°C and were analyzed within five days of collection. Case-specific death-to-collection intervals were not supplied.

Individual pairs crossed in both directions

Table 2 reports sample 1 with vitreous ethanol of 1.68 ± 0.09 g/L and blood ethanol of 1.31 ± 0.06 g/L. Sample 14 showed the opposite direction: vitreous 1.98 ± 0.16 g/L and blood 2.23 ± 0.15 g/L. These are means and standard deviations from three determinations, not measurements from three different people.

Sample 2 was particularly discordant: vitreous was below the quantification limit, while blood measured 0.35 ± 0.03 g/L. A below-LOQ result should remain below LOQ, rather than being substituted with zero to calculate a ratio. This pair does not, on its own, identify why the specimens differed.

Two reported R² values answer different questions

The analytical calibration had an R² of 0.9981. The relationship between concentrations in the actual paired specimens had an R² of 0.9227, with the reported regression equation vitreous ethanol = 1.01 × blood ethanol + 0.0479 g/L.

The calibration statistic describes instrument-method response across concentrations. The specimen statistic describes association between two matrices. Neither establishes that the two specimens give identical results in every person, nor supplies the uncertainty of an individual reconstructed blood value.

The abstract reports no statistically significant difference between matrices, but the paper does not provide a corresponding detailed equivalence analysis or individual prediction interval. Failure to demonstrate a group difference is not proof that a clinically or forensically important difference cannot occur in a particular pair.

Analytical performance does not explain ethanol origin

The laboratory used headspace gas chromatography with flame-ionization detection, a six-minute run and n-propanol as internal standard. Identification relied on retention-time comparison with standards. This was targeted quantitative ethanol analysis, rather than a broad drug screen or mass-spectral identification of every volatile.

The stated detection limit was 0.003 g/L, the quantification limit 0.01 g/L and the linear range 0.01–10 g/L. At 0.5 g/L, Table 1 reports within-day precision of 6.8% RSD and between-day precision of 7.6% RSD. No carryover was observed in the reported analyses. These performance measures support the measurement procedure; they cannot distinguish ethanol consumed during life from ethanol formed after death.

A printed ratio requires caution

For sample 5, the table lists vitreous 1.50 g/L, blood 1.64 g/L and a vitreous-to-blood ratio of 1.91. Dividing the printed concentrations gives approximately 0.91. The discrepancy should be acknowledged rather than silently accepting the ratio or presenting a corrected figure as the authors’ published value.

For case review, retain the original paired concentrations, units, collection records and analytical limits. The study did not independently establish each person’s ethanol concentration at death, quantify microbial contributions or validate impairment or cause of death from either matrix. Its useful contribution is evidence of paired-specimen behavior under the stated collection conditions.

Vitreous ethanol analysis also addresses a different question from broad vitreous drug screening; performance for one analyte does not validate all others.

Primary source

Savini F, Tartaglia A, Coccia L, et al. Ethanol Determination in Post-Mortem Samples: Correlation between Blood and Vitreous Humor Concentration. Molecules. 2020;25:2724. doi:10.3390/molecules25122724.

Later behavior after prenatal methamphetamine exposure cannot be understood from the exposure label alone. A 2016 IDEAL follow-up examined early adversity as a possible pathway linking prenatal exposure with caregiver-rated behavior at age 7.5. The results support examining the child’s environment, while falling short of proving a single causal explanation.

Who remained in the analysis?

Eze and colleagues analyzed 290 children with complete Child Behavior Checklist data and an early-adversity index: 146 classified as prenatally exposed and 144 comparisons. This was 70.4% of the original 412 mother–infant pairs. The children came from the same IDEAL cohort described in several earlier developmental reports.

Exposure classification used maternal report and/or confirmed infant meconium findings. Matching and statistical adjustment addressed selected differences, but exposure was not randomized. The study did not administer methamphetamine or standardize prenatal dose, purity or timing.

What counted as adversity?

The index summed nine binary indicators measured from birth through age three. These included poverty, caregiver changes, maternal postnatal substance use, caregiver psychological difficulties, living-environment quality, community violence and other social conditions.

This was a composite research measure. Equal contributions to its summed score do not establish that each component has the same causal effect. Nor does a higher score identify one particular family circumstance without examining the underlying records.

Which behavior outcome was measured?

Caregivers completed the Child Behavior Checklist at age 7.5. Exposed children had higher scores for externalizing problems, rule-breaking behavior and aggressive behavior. The instrument describes reported behavior; it is not direct observation of every incident or an independent diagnosis of each listed syndrome.

Caregiver reporting can be informative but can also introduce reporting bias. The study’s group averages do not establish that every exposed child had behavioral difficulties or that exposure explains a specific child’s conduct.

What did the mediation model actually find?

The researchers defined mediation statistically as a significant indirect effect. Prenatal exposure was associated with higher early adversity, and adversity was associated with higher externalizing scores. The indirect pathway for externalizing behavior was significant; the estimated proportion mediated was 34%.

The corresponding indirect effects for rule-breaking and aggressive behavior were not significant, despite reported percentage-mediated estimates of 26% and 29%. Those percentages must not be presented as three equally established findings. Their numerical existence does not remove uncertainty.

The modeled direct effect of prenatal exposure on externalizing behavior was nonsignificant. That does not prove that prenatal exposure has no direct biological effect. Statistical significance depends on measurement, model specification, sample size and the other variables included.

Why is statistical mediation not a causal allocation?

A mediation model can be consistent with a proposed pathway without ruling out unmeasured common causes, exposure misclassification or other pathways. The model did not randomize adversity, and it did not experimentally improve home conditions to test whether behavior changed.

The reported 34% therefore is not a way to divide an individual child’s difficulties into “34% environment” and “66% drug.” It describes a modeled relationship in this sample, for this outcome and set of assumptions. It is neither a biological partition nor a finding about legal responsibility.

The study strengthens the case for examining postnatal conditions in research and individual assessment. It also shows why broad claims that prenatal exposure alone determines later behavior omit important evidence and why the same cohort’s multiple publications should not be counted as independent replications.

Source

Eze N, Smith LM, LaGasse LL, et al. School-Aged Outcomes following Prenatal Methamphetamine Exposure: 7.5 Year Follow-Up From the IDEAL Study. Journal of Pediatrics. 2016;170:34–38.e1. doi:10.1016/j.jpeds.2015.11.070.

Newborn behavior changes rapidly, so a difference near birth need not remain the same one month later. A 2014 IDEAL study examined this directly in infants classified by prenatal methamphetamine exposure. Its results distinguish developmental change shared by both groups from exposure-related differences in how particular scores changed.

What did the researchers measure?

Kiblawi and colleagues used the NICU Network Neurobehavioral Scale, or NNNS, within the first five days of life and again at approximately one month. The standardized examination assesses features such as arousal, movement quality, reflexes, regulation and stress/abstinence signs.

The analysis included 380 infants with both assessments: 185 exposed and 195 comparisons. They were drawn from the larger 412-pair IDEAL cohort. The analysis was not an independent new birth cohort, and the two examinations per infant did not create 760 independent participants.

Exposure classification combined maternal self-report and/or confirmed meconium findings. Comparison infants were matched on selected characteristics. Other prenatal exposures, including alcohol, tobacco and marijuana, occurred in both groups. Examiners were masked to methamphetamine exposure status.

Which changes occurred in both groups?

After covariate adjustment, the study found time effects for higher arousal and movement quality and lower lethargy and asymmetric reflexes. A time effect means that scores changed with age across the studied infants. It does not identify methamphetamine as the cause of that change.

The investigators found no significant overall main effect of exposure on the NNNS outcomes. That null result belongs alongside the more specific findings. A narrative in which every exposed infant had an abnormal newborn profile would not reflect this complete-cohort analysis.

Why did arousal and stress receive special attention?

The exposure-by-time interactions were significant for arousal (p=0.031) and total stress (p=0.026). Arousal increased slightly in the exposed group while declining in comparisons. Stress declined more steeply in exposed infants, with estimated one-month scores essentially converging.

Those interactions address whether the change differed between groups. They are distinct from asking whether one group’s before-and-after change alone was significant. They are also distinct from proving a persistent group difference at one month, which the study did not find.

Arousal on this instrument concerns observed behavioral state. It is not a measured methamphetamine concentration, and a stress/abstinence scale score is not itself chemical proof that drug remains in the infant’s circulation.

Does convergence rule out later difficulties?

No. The observation window ended at one month for this report. The NNNS does not measure every later cognitive, educational or behavioral outcome. A nonsignificant difference at one month cannot establish lifelong equivalence, just as a subtle newborn difference cannot establish permanent injury.

The report did not analyze methamphetamine dose–response or exposure-timing differences. Much exposure ascertainment depended on self-report; meconium testing does not capture every period of pregnancy equally. Social and prenatal-care differences remained potential influences despite adjustment.

How should this historical evidence be described?

The defensible statement is that this selected cohort showed broad maturational changes and specific exposure-related arousal and stress trajectories, with no significant overall exposure effect and no persistent group separation reported at one month. The study does not determine the cause of an individual infant’s symptoms.

Follow-up findings from later IDEAL publications should be identified as later outcomes in an overlapping cohort. They can extend the developmental picture, but counting each publication as a completely independent replication would overstate the evidence base.

Source

Kiblawi ZN, Smith LM, LaGasse LL, et al. Prenatal Methamphetamine Exposure and Neonatal and Infant Neurobehavioral Outcome: Results from the IDEAL Study. Substance Abuse. 2014;35(1):68–73. doi:10.1080/08897077.2013.814614.

A small difference on a specific motor task should not be rewritten as a global cognitive deficit. Smith and colleagues’ 2011 IDEAL follow-up found evidence of lower grasping performance associated with prenatal methamphetamine exposure, particularly heavier exposure, while broader Bayley mental and psychomotor indices showed no significant exposure effects through age three.

Which children contributed data?

IDEAL enrolled 412 mother–infant pairs: 204 classified as methamphetamine-exposed and 208 matched comparisons. This analysis used subsets with completed developmental assessments. The Bayley analysis included 356 children with at least one relevant visit; the Peabody motor analysis included 350 with a one- or three-year assessment.

These were overlapping subsets of one cohort, not 706 independent children. Bayley visit counts were 331, 288 and 278 at one, two and three years. Peabody counts were 330 and 281 at one and three years. Follow-up denominators therefore changed with instrument and age.

How was exposure identified?

Classification used maternal report and/or a positive meconium screen followed by gas chromatography–mass spectrometry confirmation. Many exposed children were identified through report despite negative meconium testing. A negative meconium result did not erase the study’s reported earlier exposure history.

“Heavy” exposure meant reported use on at least three days per week across pregnancy. That is a frequency category, not a measured fetal dose or a standardized methamphetamine concentration. Tobacco, alcohol and marijuana exposure occurred in both groups and were addressed as covariates.

What did the motor tests show?

The Peabody grasping subtest assessed hand and finger coordination. At one year, the adjusted any-exposure comparison gave p=0.027, which became p=0.054 after correction for multiple testing. The heavier-exposure comparison remained significant after correction (p=0.048). Retaining those corrected results prevents a nominal finding from appearing more secure than it was.

No significant grasping difference was detected in the separate three-year comparison. Broader Peabody fine- and gross-motor scores likewise did not show significant exposure effects. A subtest result therefore cannot be substituted for the entire motor assessment.

Why did the longitudinal analysis sound different?

The repeated-measures model found lower grasping scores associated with exposure across the available one- and three-year data. That model estimates a different contrast from testing the groups at age three alone. A significant overall exposure effect can coexist with a nonsignificant single-age result.

The exposure-by-time interactions were not significant. Consequently, the absence of a significant three-year difference does not by itself prove that exposed children recovered faster or that the groups’ developmental trajectories differed. The source’s language about findings largely resolving should be read alongside that interaction result.

What did the broader developmental measures show?

Bayley Mental Development Index and Psychomotor Development Index comparisons were nonsignificant at individual ages and in longitudinal models, including analyses of heavier exposure. These are important null findings. They do not prove that every developmental domain was unaffected or exclude difficulties emerging after age three.

Observational exposure assignment, coexposures, selective follow-up and imperfect exposure measurement constrain causality. The researchers adjusted for several social and biological variables, but adjustment cannot measure every relevant difference. For an individual child, the appropriate evidence remains the child’s own developmental assessment; an exposure label cannot supply a diagnosis from a group average.

Source

Smith LM, LaGasse LL, Derauf C, et al. Motor and Cognitive Outcomes Through Three Years Of Age In Children Exposed To Prenatal Methamphetamine. Neurotoxicology and Teratology. 2011;33(1):176–184. doi:10.1016/j.ntt.2010.10.004.

Combining all prenatal methamphetamine exposure into one category can hide differences in timing and in the comparison population. Wright and colleagues’ 2015 study of a Honolulu prenatal clinic illustrates both problems. Its findings concern a historical clinical cohort, not a randomized test of exposure or a prediction for an individual pregnancy.

What population did the study follow?

The investigators retrospectively analyzed clinical data collected prospectively during prenatal care from 2007 through 2013. The live-birth analysis included 251 infants: 144 with recorded prenatal methamphetamine exposure and 107 without it. A subgroup of 59 infants had no recorded drug exposure. The 59 were part of the comparison population, not an additional independent group to add to 251.

The clinic provided prenatal care, addiction-related services and practical support. Many participants experienced housing insecurity and socioeconomic disadvantage. Women entering this clinic, and particularly those who remained in care, may differ from people not seeking similar services.

Which birth-weight comparison was null?

Mean birth weight was 3,159 g in the methamphetamine-exposed group and 3,168 g in the non-methamphetamine group (p=0.9). That broad comparison did not demonstrate a difference. Against the no-drug subgroup, the exposed mean was lower: 3,159 versus 3,321 g (p=0.04).

These findings are compatible because the control groups differ. “No methamphetamine exposure” could include other drug or tobacco exposure and prior addiction history. Reporting only the significant comparison would conceal an important null finding and alter what the study actually tested.

What did timing add?

Among the 144 exposed infants, recorded exposure ended in the first trimester for 50, continued into the second for 45, and continued into the third but was negative at delivery for 29. Twenty were classified as having positive toxicology at delivery.

The study associated continued use through delivery with shorter gestation and smaller infants. The delivery-positive subgroup’s mean birth weight was 2,932 g, compared with 3,300 g after first-trimester-only exposure (p=0.01). Those are group observations, not estimates of how many grams a specified dose would change an individual infant’s weight.

The source’s exposure terminology needs care: its abstract mentions meconium or urine in describing birth toxicology, while the methods define the delivery-positive classification using maternal or neonatal urine because meconium can reflect earlier exposure. The classification should not be treated as a validated exact last-use clock.

What did adjustment change?

The adjusted analysis associated persistent exposure with preterm delivery, but not with small-for-gestational-age classification. Persistent smoking, rather than methamphetamine, was associated with that latter outcome. Birth weight, gestational age and size relative to gestational age are different endpoints.

The authors also found that continuing users were more likely to have inadequate prenatal care. Statistical adjustment addresses measured covariates; it does not make the groups exchangeable as though exposure cessation had been randomized.

What can be concluded about stopping use?

Participants who stopped use had more favorable observed birth outcomes than those continuing through delivery. That is clinically meaningful historical evidence, but cessation occurred alongside differences in care engagement and potentially other unmeasured factors. The study cannot isolate how much of the association came from stopping methamphetamine alone.

Self-report, incomplete alcohol information, absent maternal weight-gain data and possible dating error in pregnancies entering care late limit interpretation. The study’s null results do not establish safety of prenatal exposure. Its useful lesson is to retain timing, comparator composition and the particular outcome before drawing a causal conclusion.

Source

Wright TE, Schuetter R, Tellei J, Sauvage L. Methamphetamines and Pregnancy Outcomes. Journal of Addiction Medicine. 2015;9(2):111–117. doi:10.1097/ADM.0000000000000101.

A national mortality trend can identify a major public-health pattern without showing how two drugs entered an individual person’s body. Hoopsick and Yockey’s 2023 analysis found increasing opioid co-involvement in deaths classified as methamphetamine-related. Understanding the coding method is essential before interpreting its percentages as chemical or causal proof.

What records did the researchers analyze?

The study used CDC WONDER multiple-cause death-certificate data for U.S. residents aged 15–74 from 1999 through 2021. Data through 2020 were final; 2021 data were provisional when analyzed. This is a historical descriptive epidemiologic study, not an experiment or a new laboratory analysis of retained specimens.

The authors selected poisoning deaths across specified intent categories, then used ICD-10 code T43.6, “psychostimulants with abuse potential,” to operationalize methamphetamine-related deaths. The title’s methamphetamine label therefore rests on a coded psychostimulant category. The method does not present an individually measured methamphetamine concentration for every record.

How was opioid co-involvement defined?

The analysis used T40.1 for heroin and T40.4 for other synthetic narcotics, described in the paper in relation to fentanyl and its analogs. These are categories in a mortality database. Their presence in a coded record is different from a standardized assay identifying one exact synthetic opioid in one specified specimen.

A transparent account preserves the authors’ operational terminology while explaining the category boundaries. Substituting “laboratory-confirmed methamphetamine plus illicit fentanyl in every case” would claim more specificity than this dataset supplies.

What did the historical trends show?

The selected records included 135,433 deaths across the period, with heroin or synthetic-narcotic co-involvement in 42.8% overall. The annual proportion with that co-involvement reached 61.2% in 2021. The overall-period percentage and the last-year percentage describe different denominators and should not be interchanged.

The reported age-adjusted mortality rate increased from 0.27 per 100,000 population in 1999 to 13.93 in 2021. A population mortality rate is not the probability that a person who uses methamphetamine will die: the study did not measure the number of exposed people or their individual doses as its denominator.

Does co-involvement identify contamination?

No. Intentional co-use, unintentional exposure and other circumstances may all be compatible with co-involvement in mortality records. The study did not test purchased drug products, interview every decedent or determine a verified sequence and route of administration.

Nor can an aggregate association assign the relative causal contribution of each detected substance in a particular death. That question requires the individual investigation, including specimen findings, medical history, scene evidence and competing explanations. Population data help frame a question; they do not perform that reconstruction.

What can affect the counts?

The authors noted exclusions of nonresidents and deaths without relevant toxicology or drug-specific information, as well as reporting lags in provisional 2021 data. Differences in testing and certification can influence which drugs appear in the coded record. Missing drug information should not be silently treated as proof that a substance was absent.

The study supports concern about a rising overlap between stimulant-coded and opioid-coded fatal poisonings during its observation period. Its practical value depends on retaining the age range, historical dates, coding definitions and uncertainty about exposure circumstances. The reported 2021 peak is not a statement about present-day rates.

Source

Hoopsick RA, Yockey RA. Methamphetamine-Related Mortality in the United States: Co-Involvement of Heroin and Fentanyl, 1999–2021. American Journal of Public Health. 2023;113(4):416–419. doi:10.2105/AJPH.2022.307212.

“How many adults use methamphetamine?” and “How many adults with methamphetamine use disorder receive treatment?” require different denominators. A 2020 report by Jones, Compton and Mustaquim demonstrates why the distinction matters. It analyzed U.S. survey data from 2015–2018, so its figures are historical estimates rather than current prevalence.

Who was actually surveyed?

The analysis used 171,766 adults participating in the National Surveys on Drug Use and Health. The underlying surveys sampled noninstitutionalized U.S. civilians and used a probability design and weights to generate population estimates. The adult analysis included people aged eighteen and older.

The estimated 1,626,200 adults reporting past-year methamphetamine use was an annual average for the pooled period. It was not the unweighted number of respondents who reported use, and it was not a sum of four nonoverlapping annual populations. Someone represented in one annual estimate could also use methamphetamine in another year.

What did 6.6 per 1,000 mean?

The estimated annual average rate of past-year use was 6.6 per 1,000 adults, with a 95% confidence interval of 6.1–7.1. The denominator was the represented adult population, not only people using drugs, treatment entrants or people stopped while driving.

The estimate came from self-reported use. The study did not administer methamphetamine or establish exposure with quantitative blood testing. It therefore cannot identify a dose, purity, concentration, last-use time or impairment level for the people represented.

Why is 52.9% a different figure?

Among adults reporting past-year methamphetamine use, 52.9% met the survey’s criteria for past-year methamphetamine use disorder. The denominator had now narrowed to people reporting use. This percentage does not mean 52.9% of all U.S. adults had that disorder.

The disorder classification was based on self-reported answers corresponding to DSM-IV criteria. The authors cautioned that it was not a count of diagnoses made by health professionals. Treating every past-year exposure as a disorder would erase the distinction the study deliberately measured.

Frequency also varied: 36.2% of past-year users reported use on 1–29 days, while 27.3% reported at least 200 days. Neither “any use” nor one disorder label adequately summarizes the full distribution of reported use patterns.

What does the treatment figure describe?

Among adults meeting the survey definition of past-year methamphetamine use disorder, an estimated 31.5% received any substance-use treatment in the preceding year. That is a third denominator. “Any substance-use treatment” also does not establish the content, intensity or effectiveness of methamphetamine-specific care.

Subtracting 31.5% from 100% describes lack of reported treatment within this operational group. It cannot independently establish that every remaining person sought treatment, had an unmet clinical need of the same severity, or would respond to one particular program.

Which populations and explanations remain outside the estimate?

The surveys did not include unsheltered homeless people, active-duty military personnel or people living in institutions such as prisons. The average weighted response rate was approximately 51%. Self-report, nonresponse and population exclusions can affect estimates and generalizability.

The analysis found associations with demographic, mental-health and other substance-use characteristics. Its cross-sectional design could not establish why those associations occurred. A historical household estimate is useful population evidence when its time frame, sampling population and denominator remain attached; it cannot diagnose or characterize a specific individual.

Source

Jones CM, Compton WM, Mustaquim D. Patterns and Characteristics of Methamphetamine Use Among Adults—United States, 2015–2018. MMWR. 2020;69:317–323. doi:10.15585/mmwr.mm6912a1.

A treatment review can show where research exists without establishing which treatment works best. Hersi and colleagues’ 2023 scoping review of problematic methamphetamine use illustrates that distinction. Its evidence maps identified potentially favorable findings across many interventions, but the authors did not present those maps as reliable treatment rankings.

What did the review include?

The review identified two systematic reviews, one clinical practice guideline and 54 primary controlled studies reported in 69 publications. Those are different units. Several articles can describe one study, and a systematic review can include trials also discussed elsewhere. Adding all publications together would exaggerate the number of independent tests.

The updated searches ran through February 2022. Eligible primary studies addressed methamphetamine use disorder or problematic methamphetamine use, with rules for separating relevant participants from broader stimulant samples. Most outcomes required follow-up of at least three months. The review excluded certain approaches, including exercise, transcranial magnetic stimulation and art therapies. Its map therefore was not a census of every possible intervention.

What did a favorable direction mean?

For the primary-study synthesis, the team used vote counting by direction of effect. A result could favor intervention or comparison, show no difference, or remain unclear. Crucially, classification did not incorporate statistical significance, effect magnitude or differences in study sample size.

A small favorable estimate with substantial uncertainty could therefore point in the same direction as a large, precise benefit. The authors explicitly warned that a direction alone might represent a clinically unimportant difference. Counting favorable directions cannot tell a reader how many people benefit, how much outcomes improve, or how confidently a difference excludes chance.

Why were the treatments difficult to compare?

The review identified 37 approaches to measuring methamphetamine use. An intervention could look favorable on one measure and less favorable on another. Studies also differed in intervention delivery, comparators, populations and assessment schedules.

Even apparently similar abstinence outcomes could require different numbers of submitted negative urine samples. A person meeting a less demanding specimen rule is not necessarily comparable to someone meeting a stricter rule in another trial. Treatment retention, reduced use, craving and abstinence are related but distinct outcomes.

These differences also affected the feasibility of network meta-analysis. Such an analysis needs more than a connected diagram of treatments: the studies must support sufficiently credible comparisons. The authors judged the available evidence unsuitable for robust network meta-analyses.

What quality checks were performed?

The researchers appraised systematic reviews with AMSTAR-2 and the guideline with AGREE-2. They did not assess the quality of individual primary studies, consistent with their scoping approach. A colorful primary-study evidence map should not be read as though each contributing trial had passed a uniform risk-of-bias assessment.

The review also found sparse information for several priority populations, including pregnant people and people in correctional settings. English- and French-language restrictions, differences in reporting and single-study interventions further limited coverage and certainty.

How can the map be used responsibly?

It is useful for locating research, identifying neglected populations and choosing studies for closer appraisal. It is weaker support for statements that one treatment is definitively superior or that nearly every intervention is effective because at least one result points in a favorable direction.

For an individual treatment claim, the next task is to examine the original comparison, endpoint, effect size, uncertainty, missing data and harms. This review describes evidence available through its search period; it does not supply current prescribing guidance or replace a direct assessment of a particular trial.

Source

Hersi M, Corace K, Hamel C, et al. Psychosocial and pharmacologic interventions for problematic methamphetamine use: Findings from a scoping review of the literature. PLOS ONE. 2023;18(10):e0292745. doi:10.1371/journal.pone.0292745.

A 2015 randomized trial tested a plausible hypothesis: bupropion might improve abstinence among people using methamphetamine less than daily. The primary result did not support that benefit. Medication adherence was low, but that limitation does not convert the negative comparison into evidence that the drug worked in an unobserved fully adherent population.

Why select non-daily users?

Earlier findings had suggested possible benefit in a lower-frequency subgroup. Anderson and colleagues therefore recruited treatment-seeking adults with methamphetamine dependence who reported use on no more than 29 of the 30 days before consent. “Non-daily” covered a wide range of patterns; it did not mean only occasional exposure.

The analysis included 204 randomized participants who took a first dose: 100 assigned oral sustained-release bupropion, 150 mg twice daily, and 104 assigned matching placebo. Treatment lasted twelve weeks, followed by four weeks of follow-up. Participants also received frequent clinic visits and group relapse-prevention therapy. This was a medication-plus-services comparison against placebo-plus-services.

What counted as abstinence?

The primary endpoint required at least two urine specimens in each of weeks 11 and 12, with every specimen in those weeks negative under the study’s methamphetamine rule. Dropping out before the terminal assessment counted as failure. This is a specific terminal-abstinence endpoint, not a claim of continuous abstinence throughout all twelve weeks.

Urine immunoassay used a 300 ng/mL decision level for methamphetamine and/or amphetamine, with positive screens followed by gas chromatography–mass spectrometry. The reported confirmatory methamphetamine quantification limit was 78 ng/mL. An analytical quantification limit and the endpoint’s 300 ng/mL classification rule served different purposes; neither was a blood impairment threshold.

What did the trial find?

Terminal abstinence occurred in 14/100 bupropion participants and 20/104 placebo participants, approximately 14% versus 19% (p=0.32). Twelve-week completion was 57% in each group. The study did not demonstrate either an abstinence or retention advantage.

Among participants reporting use on no more than 18 of the previous 30 days, success was 13/65 with bupropion and 17/76 with placebo (p=0.73). Lower baseline use predicted better outcomes when groups were combined. That prognostic association is different from evidence that lower-frequency users specifically benefited from bupropion.

What does the adherence assay add?

The researchers measured bupropion in urine, using a 5 ng/mL lower quantification limit. Their adherence rule required detectable medication in specified proportions of specimens during earlier and terminal treatment weeks. Only 47/100 active participants met it. No corresponding biochemical marker measured placebo adherence.

Low exposure to assigned medication can dilute an intention-to-treat treatment effect. But selecting adherent participants afterward also selects for attendance, motivation, stability and other factors related to outcome. Without a comparable control strategy, better outcomes among selected adherent people cannot be attributed solely to medication.

What uncertainty remains?

Recruitment criteria were relaxed during the study to permit corroborated use without a positive screening urine. Some participants consequently had no positive urine throughout screening or treatment. Attrition, greater-than-expected placebo success and imperfect adherence reduced the study’s ability to detect some benefits.

Bupropion was discontinued for several adverse events, including two seizures; one occurred after a participant stopped an undisclosed anticonvulsant. These observations require context rather than a claim that every event had a single cause. The historical evidence supports neither an established abstinence benefit nor a categorical conclusion that bupropion could never help under different conditions.

Source

Anderson AL, Li SH, Markova D, et al. Bupropion for the Treatment of Methamphetamine Dependence in Non-Daily Users: a Randomized, Double-Blind, Placebo-Controlled Trial. Drug and Alcohol Dependence. 2015;150:170–174. doi:10.1016/j.drugalcdep.2015.01.036.

Delivering a medication reliably and demonstrating that it works are separate achievements. A placebo-controlled trial of extended-release naltrexone in 100 actively using, methamphetamine-dependent men who have sex with men achieved high injection adherence but did not demonstrate a reduction in methamphetamine-positive urine results relative to placebo.

Coffin and colleagues’ paper appeared online in 2017 and in the 2018 volume of Addiction. Its result concerns naltrexone alone, under a particular schedule and in a selected population. It should retain that identity when compared with studies combining naltrexone with another medication.

What did the randomized comparison involve?

Fifty participants received 380 mg of extended-release naltrexone and fifty received matching placebo. Investigators administered three intramuscular gluteal injections at four-week intervals over twelve weeks. Both groups received weekly visits, urine testing and approximately thirty minutes of substance-use counseling using cognitive behavioral and motivational approaches.

Participants wanted to reduce or stop methamphetamine use and met the study’s dependence criteria. Enrollment also required reported sexual activity with men while under methamphetamine’s influence during the preceding six months. The study excluded several conditions that could compromise safe participation. This was not a population sample of everyone using methamphetamine.

What happened to the urine results?

The reported urine-positivity trajectory comparison gave a ratio of 0.95, with a 95% confidence interval of 0.76–1.20. The interval included no difference. Observed positivity declined in both groups, from 78% to 70% with naltrexone and from 74% to 64% with placebo.

Improvement within the active group therefore cannot establish a medication effect. The relevant comparison is whether the active group improved more than its randomized control. Counseling, repeated contact, changes in motivation and other shared influences could contribute to changes in both groups.

Craving and several self-reported risk measures also declined without a significant advantage for naltrexone. Urine positivity was a repeated categorical testing outcome, not a measurement of dose consumed, circulating methamphetamine concentration or functioning at a particular event.

Why does adherence matter here?

Injection adherence was 96.7% in the naltrexone group and 91.3% with placebo. Ninety percent of active participants received all three injections. High delivery rates make it harder to explain the null result solely by saying that participants generally failed to receive medication.

The investigators also examined cumulative injections and several sensitivity analyses, including treating missing urines as positive. These did not reveal a significant benefit. Adherence strengthens the interpretation of the tested regimen’s result; it does not establish that every biological response was identical or that every conceivable treatment effect was excluded.

How far does the null finding extend?

The trial was designed to detect a substantial reduction in urine positivity. A nonsignificant result is not proof of an exactly zero effect. Its confidence interval, power assumptions and selected population remain relevant. Most participants had HIV-positive serostatus, and all were recruited in a particular San Francisco setting.

The authors specifically identified naltrexone in isolation as a limitation. A later successful combination trial would not retroactively make this monotherapy trial positive, nor would this null trial invalidate a different combination, dosing interval or population.

No serious adverse event was judged related to study medication, and adverse-event frequencies did not differ significantly between groups. A hundred-person, twelve-week observation cannot establish absence of uncommon harms. The useful historical conclusion is precise: reliable delivery of this monthly monotherapy did not translate into a demonstrated advantage on the measured methamphetamine-use outcomes.

Source

Coffin PO, Santos GM, Hern J, et al. Extended-Release Naltrexone for Methamphetamine Dependence among Men Who Have Sex with Men: A Randomized Placebo-Controlled Trial. Addiction. 2018;113(2):268–278; online 2017. doi:10.1111/add.13950.