Author: toxlaw

“Digital treatment works” is too broad a conclusion for a literature containing text messages, apps, virtual therapists, web programs and virtual reality. A 2026 scoping review offers a more useful question: who participated, what counted as success and who remained available to report it?

What did this review map?

Fletcher and colleagues searched four databases through December 18, 2024. Their review, published in January 2026, included 17 records describing 15 studies and 13 distinct digital health interventions. The aggregate prospective sample was 1,269 adults across six countries; a historical control group of 102 was excluded from that aggregate.

Eight of the 15 studies were randomized trials. The remaining designs could address feasibility or acceptability without providing the same causal comparison. This was a descriptive scoping review, not a pooled estimate of treatment benefit or a head-to-head ranking of technologies.

Were all participants receiving treatment for the same condition?

No. Of the 1,269 participants, 772 met inclusion criteria involving methamphetamine use, while 497 met diagnostic criteria for methamphetamine use disorder. Those populations may have different needs, baseline severity and reasons for using an intervention. An app studied in people not seeking formal treatment is not automatically validated for a highly selected inpatient population, or vice versa.

The review also focused on self-management technologies. Primary telehealth interventions were excluded unless they incorporated a qualifying self-directed digital component. Its findings should therefore not be presented as a verdict on all remote clinical care.

Who was underrepresented?

Among the 1,217 participants in studies reporting gender, 180 were women: 14.8%. That percentage has a different denominator from the full sample of 1,269. Some interventions were studied entirely in men or in specifically recruited groups of men who have sex with men.

Population targeting can be appropriate for the question being studied. The limitation arises when findings are generalized beyond that population. The review does not demonstrate that the same acceptability, use patterns or outcomes apply to women, people with limited digital access or other groups poorly represented in the samples.

Why are satisfaction and attrition a difficult combination?

Reported dropout ranged from 7.3% to 67.7% across differing interventions and observation periods. That range is not a pooled probability of digital-treatment failure. It shows substantial variation and makes the definition and timing of dropout important.

The review describes a chatbot study with high satisfaction among respondents, while satisfaction was not collected from people who dropped out. Such results describe those who remained reachable. They cannot establish equally high satisfaction among everyone who started. Financial incentives, clinic support and device access can also shape engagement.

Which outcomes should remain separate?

Craving ratings, cognitive task performance, help-seeking, self-reported use and methamphetamine-positive urine tests answer different questions. The review found mixed clinical results. Some interventions changed selected outcomes without demonstrating a reduction in drug use, and favorable subgroup findings were not universal effects.

For example, willingness to use a virtual therapist is evidence of acceptability, not proof of sustained abstinence. Reduced cue-induced craving during a virtual-reality session does not by itself show fewer subsequent use days. Improvements from baseline in an uncontrolled pilot cannot isolate the technology’s effect from other care or the passage of time.

What would make a digital claim more persuasive?

A meaningful evaluation would identify the intended population, comparator, intervention support, actual engagement, missing-data approach and follow-up duration. It would specify whether the primary aim was access, symptom relief or reduced use, rather than allowing any favorable result to stand in for all three.

The review supports further development and testing of digital options. It does not establish that an arbitrary methamphetamine app is effective, that human support is dispensable or that improved digital engagement demonstrates functional fitness or absence of impairment.

Source

Fletcher K et al. Digital health interventions for people who use methamphetamine: a scoping review. Frontiers in Psychiatry. 2026;16:1658021. doi:10.3389/fpsyt.2025.1658021. Evidence map with searches ending in December 2024.

Finding a chemical mark on DNA is not the same as finding a mutation, demonstrating brain damage or proving how a child will develop. A study of prenatal methamphetamine exposure and childhood DNA methylation shows why specimen, timing and functional validation matter.

Who was studied, and when?

Oni-Orisan and colleagues examined 100 children aged ten to eleven from the California and Hawaii sites of the IDEAL longitudinal cohort: 55 with prenatal methamphetamine exposure and 45 comparison children. Exposure was established at birth by maternal self-report and/or meconium screening with gas chromatography–mass spectrometry confirmation. This was an observational follow-up, not a controlled exposure experiment.

At the childhood visit, researchers obtained saliva-derived, buccal DNA and measured methylation at four CpG sites in the HSD11B2 gene region using bisulfite pyrosequencing. They also used an early-adversity index covering birth through age five. The measurement was not brain tissue, and there was no baseline methylation measurement at birth showing the same mark persisting continuously for a decade.

What association was reported?

The main reported methylation difference was at CpG site 2. The abstract gives methylation values of 1.4% in exposed children and 0.31% in comparison children. In the final adjusted model, prenatal exposure was associated with a regression coefficient of 0.32, 95% confidence interval 0.04–0.60, p = 0.03. Early adversity also remained associated with methylation.

Those model coefficients concern transformed methylation data: the investigators winsorized values and used natural-log transformations. The coefficient 0.32 should not be recast as a 32-percentage-point rise in raw methylation. One significant site among four is also a more specific observation than a claim that the whole gene or genome was broadly altered.

Why do the intermediate models and null findings matter?

The prenatal-exposure association was no longer statistically significant when early adversity entered the second model; it became significant again after adding the hair-cortisone measure and remained so after further covariates. That sensitivity to model specification is part of the evidence. The final result should not be described as unaffected by adjustment.

There was no significant prenatal-exposure-by-adversity interaction. Hair cortisone itself was not significantly associated with methylation in the reported model. Thus the study did not demonstrate that adversity amplified the exposure association or that the measured methylation difference produced the measured stress-marker level.

What happened to the proposed cortisol measurement?

Hair was obtained from 87 of the 100 children. Sixty-three specimens had cortisol reported as zero, indicating nondetection, while 72 had positive cortisone values. The investigators therefore used cortisone, measured by liquid chromatography–tandem mass spectrometry in a proximal three-centimeter hair segment.

Cortisol and cortisone are different analytes. A nondetected cortisol result is not proof that a child had no physiological cortisol, and replacing the planned stress-related measure affects interpretation. Missing hair specimens and assay detectability should remain visible when describing the model.

Does this establish a lasting biological mechanism?

The authors proposed biological embedding of prenatal exposure and postnatal adversity. The study supports an association consistent with further investigation of that hypothesis. It did not directly measure gene expression, enzyme function, brain methylation or a methylation-mediated behavioral outcome in this analysis.

The sample was small, came from only two original recruitment sites, and differed on other prenatal exposures and social characteristics. Statistical adjustment does not reproduce randomization. Tissue specificity and the small magnitude of the methylation differences further limit inference. These results are not a validated test of an individual child’s exposure, injury, future behavior or parenting environment.

Source

Oni-Orisan OO et al. DNA methylation in Children with Prenatal Methamphetamine Exposure and Environmental Adversity. Pediatric Research. 2021;89:1152–1156; published online in 2020. doi:10.1038/s41390-020-1058-4. Historical observational human evidence.

Methamphetamine use was associated with poorer retention in opioid medication treatment across eight studies summarized in a 2023 scoping review. That consistent direction deserves attention, but it does not establish that methamphetamine alone caused a person to leave care or that opioid medication was ineffective.

What evidence did the review include?

Russell and colleagues searched through May 2023 for studies comparing opioid-medication patients with and without methamphetamine use. Eight studies qualified. Six involved methadone, one buprenorphine and one a broader national medication-treatment dataset. The settings included Canada, the United States, China and Iran. The latest underlying data were collected in 2018, making this historical evidence rather than a measurement of present-day retention.

The evidence was observational. Methamphetamine exposure was generally self-reported over differing time windows; one study used rapid urine testing. The review deliberately excluded studies that reported only undifferentiated “amphetamines” without methamphetamine-specific results. It did not conduct a pooled meta-analysis because the treatments and retention definitions were heterogeneous.

What did “discontinuation” actually mean?

It could mean no active buprenorphine prescription or program contact for more than 30 days, no longer reporting methadone at a later interview, or a recorded treatment discharge. In the national discharge dataset, reasons included completion, dropout, facility termination, transfer, incarceration and other reasons.

Those events are not clinically interchangeable. A transfer may preserve access to medication elsewhere; an administrative discharge may reflect a program rule. A retention statistic therefore needs its operational definition before it can be used to describe a particular patient’s course.

How large were the associations?

As summarized in the review, a Washington buprenorphine study of 799 people found an adjusted hazard ratio of 2.39 for discharge among those reporting past-month methamphetamine use, with a 95% confidence interval of 1.94–2.93. Its outcome incorporated the prescription/contact definition above.

A separate Vancouver methadone study reported an adjusted hazard ratio of 1.38, 95% confidence interval 1.03–1.85, for the higher-frequency methamphetamine category. The national treatment-discharge analysis reported an odds ratio of 0.48, 95% confidence interval 0.45–0.51, for six-month retention. These are estimates from different studies, with different adjustments and endpoints. Odds ratios and hazard ratios should not be averaged casually or translated into a universal percentage chance of dropout.

Why does a frequency gradient not settle causation?

Several studies found greater discontinuation with more frequent reported methamphetamine use. That pattern strengthens the reason to study the association, but frequency can also track housing instability, illness severity, other drug use, financial pressure and difficulty reaching services. Statistical adjustment cannot remove every unmeasured difference.

Service design may also contribute. The review discusses variation in medication access and programming between jurisdictions. A result about retention combines patients’ circumstances with what a treatment system requires and offers. It is not simply a laboratory experiment on a drug’s pharmacological effect.

How can these findings be used responsibly?

The evidence identifies a population that may face additional barriers to staying connected with care. It does not show that stopping opioid medication improves outcomes for people who use methamphetamine, and no such inference follows from these comparisons. Nor does a positive urine result demonstrate unwillingness to engage, a diagnosis of concurrent methamphetamine use disorder or impairment during a visit.

For an individual record review, distinguish the measured use period, medication, contact history, reason for discharge and availability of alternative care. The review supplies a research association, not a causal explanation for every interruption.

Source

Russell C et al. The impact of methamphetamine use on medications for opioid use disorder (MOUD) treatment retention: a scoping review. Addiction Science & Clinical Practice. 2023;18:48. doi:10.1186/s13722-023-00402-0. Review of historical observational human evidence.

A 2019 mouse experiment found striking sex differences after repeated methamphetamine administration. Its value is as a controlled model of possible cardiac toxicity, not a calculator of human risk or proof that women are protected.

Which animals received which exposure?

Marcinko and colleagues studied C57BL/6 mice beginning at eight to ten weeks of age. Investigators administered (+)-methamphetamine hydrochloride by weekly intraperitoneal injection, with phosphate-buffered saline injections as the comparison. The dose increased over time. The two-month regimen reached 35 mg/kg; the five-month regimen reached 40 mg/kg. The paper describes an overall escalation beginning around 5 mg/kg.

These were intermittent injections into the abdominal cavity. They were not human oral treatment, smoking or injection-use histories, and the milligrams per kilogram cannot be transferred directly into a human toxic or lethal dose. Exposure schedule and species remain part of the finding.

What happened at two and five months?

There were no deaths in either sex in the two-month experiment. Male fractional shortening was reduced, but many other echocardiographic comparisons were not statistically significant. At five months, the authors reported 56% mortality among methamphetamine-treated males and no deaths among treated females. The survival figure lists 16 treated males and seven treated females, with six male and four female saline controls.

The longer experiment also showed greater male cardiac enlargement and functional changes. At five months, reported mean ejection fractions were 90.6% in male controls and 83.9% in treated males, with corresponding fractional shortening of 60.7% and 51.8%. These are mouse echocardiographic values, not clinical thresholds for human heart failure.

Female functional differences at the five-month endpoint generally did not reach statistical significance. That is not proof of zero effect: the groups were small, and a nonsignificant comparison does not establish equal susceptibility.

Why does survival complicate the heart measurements?

The animals available for late measurements were survivors. If animals that died had more severe dysfunction, measurements among survivors could understate the full effect. The investigators explicitly raised that possibility without claiming to have proved it.

Histology requires additional care. The paper’s discussion describes fibrosis in a single surviving male in the relevant material and says that observation was not amenable to statistical evaluation. A photograph demonstrating collagen deposition is not a quantitative estimate of how often fibrosis occurred across all treated animals. The study also included two distinct five-month male trials but only one female trial, which complicates a simple balanced comparison.

Did the study prove an estrogen mechanism?

No. The authors discussed hormonal and metabolic explanations and measured changes in cardiac gene expression. They did not establish the observed sex difference by experimentally isolating an estrogen mechanism in this study. A proposed explanation must remain separate from the controlled evidence that the exposure regimens produced different observed outcomes.

Small sample sizes, multiple functional and transcriptional measurements, uneven replication and survivor selection all matter. The results are useful for developing mechanistic questions and selecting future experiments, but do not validate a clinical prediction rule.

What can be concluded for forensic interpretation?

The experiment supports sex-dependent outcomes under a particular escalating mouse exposure schedule. It does not establish a safe human concentration, determine whether methamphetamine caused an individual death or show that one sex cannot develop cardiomyopathy. Human records, alternative causes, exposure evidence and the actual cardiac findings still require independent evaluation.

Source

Marcinko MC, Darrow AL, Tuia AJ, Shohet RV. Sex influences susceptibility to methamphetamine cardiomyopathy in mice. Physiological Reports. 2019;7:e14036. doi:10.14814/phy2.14036. Historical controlled animal evidence.

A reported “3.421-fold” association between methamphetamine-related disorders and cardiomyopathy is not a statement that every exposed person has a 3.421-fold probability of developing heart disease. Reading the underlying Taiwanese claims study requires separating diagnostic codes, observed events, person-time rates and an adjusted hazard model.

What population did the study follow?

Yu and colleagues analyzed historical Taiwanese insurance records from 2000–2015, matching 17,071 adults with methamphetamine-related disorder diagnoses to a comparison group at a 1:4 ratio by age, sex and inclusion year. The abstract and main text report 68,264 controls. Some table headings instead print 68,284; the stated total of 85,355 and the 1:4 design correspond to 68,264. That discrepancy should remain visible rather than silently becoming a new denominator.

The exposure was an administrative diagnosis involving dependence, abuse or psychosis categories. It was not a standardized administered dose, a measured blood concentration or verified consumption by a defined route. Absence of a recorded disorder diagnosis also does not prove a person had never used methamphetamine.

What do the events and rates show?

The paper reports 153 cardiomyopathy events in the diagnosed group and 274 in the comparison group. Table 4 gives 198,273.14 and 793,065.24 person-years, respectively. Dividing events by these denominators produces approximately 77.17 and 34.55 events per 100,000 person-years, as that table reports.

A later paragraph instead describes rates of 0.77 and 0.34 per 100,000 person-years. Those figures are inconsistent with both the table and the event/person-time arithmetic by roughly a factor of 100. They should not be repeated as interchangeable estimates. The event counts are not percentages, and person-year rates are not fixed-period individual probabilities.

What does the adjusted hazard ratio add?

The Cox analysis reported an adjusted hazard ratio of 3.421, with a 95% confidence interval of 1.589–5.014. The model incorporated recorded demographic, comorbidity and health-system variables. A hazard ratio compares modeled event occurrence over follow-up; it is not the crude ratio of the two observed rates and should not be multiplied directly by someone’s presumed lifetime risk.

The association is relevant evidence, but adjustment only addresses measured variables under the model’s assumptions. The study lacked detailed alcohol consumption, lifestyle, genetic, psychosocial and exposure-severity information. It also relied on people coming into medical care. Differences in diagnosis and surveillance may matter alongside biological effects.

Do subgroup labels establish a dose–response relationship?

No. The reported hazard ratios differed across dependence, abuse and psychosis codes, but those codes are not measured dose levels. The study did not supply comparable milligrams, frequency, route or cumulative exposure for each person. Treating the categories as a calibrated exposure ladder would add information the database did not contain.

Likewise, a sex association in this human claims model is a different question from sex differences in a controlled mouse experiment. Neither can be used to declare universal male or female susceptibility without attention to the population, outcome and comparison.

How should this paper inform a case review?

It can support a carefully qualified statement that recorded methamphetamine-related disorders were associated with subsequent recorded cardiomyopathy in this historical cohort. It cannot assign the cause of one person’s cardiomyopathy, reconstruct their dose or demonstrate impairment from a positive toxicology result. The reporting inconsistencies also make checking the original tables essential before quoting absolute rates.

Source

Yu PC et al. Increased risk of cardiomyopathy in individuals with methamphetamine related disorders in Taiwan. Scientific Reports. 2025;15:11449. doi:10.1038/s41598-025-94591-0. Observational human claims evidence using 2000–2015 records.

A small open-label medication study can justify a larger experiment without establishing that a treatment works. A subsequent randomized trial of modafinil for methamphetamine dependence illustrates why that distinction matters: favorable-looking subgroup patterns did not overturn the trial’s negative overall result.

What did the investigators actually compare?

Heinzerling and colleagues reported a historical, randomized, double-blind, placebo-controlled human trial in 2010. Of 207 people entering screening, 71 were randomized: 34 to modafinil and 37 to placebo. Both groups also received access to weekly cognitive behavioral therapy and contingency management, which rewarded methamphetamine-negative urine specimens. The medication comparison therefore tested modafinil’s added effect within that treatment platform.

Oral modafinil started at 200 mg daily for three days, increased to 400 mg each morning, and returned to 200 mg for the final three days of the 12-week medication phase. Participants attended three times weekly for urine testing. Significant medical and psychiatric exclusions and exclusions for several other substance dependencies narrowed the population studied.

What were the main results?

The investigators found no statistically significant difference in aggregate urine outcomes in the planned full-sample analyses. In their longitudinal model, the odds ratio for providing a methamphetamine-free urine screen with modafinil versus placebo was 0.78, with a 95% confidence interval of 0.39–1.56 and p = 0.49. That interval permits appreciably different effects in either direction; it does not establish equivalence.

Completion was 41% with modafinil and 35% with placebo, p = 0.60. Mean retention was 57 versus 47 days, p = 0.16. There was also no significant medication-group effect on craving or depressive symptoms. Improvements over time within treatment cannot, by themselves, be assigned to modafinil when the comparison group also changes.

Why did counseling attendance attract attention?

Exploratory analyses divided participants by baseline use frequency and by attendance at zero to two versus at least three cognitive behavioral therapy sessions. Some numerical patterns favored modafinil among people with low attendance or higher baseline use. The reported aggregate urine and retention comparisons did not establish significant benefit in those small subgroups.

More fundamentally, attendance was behavior occurring during the trial, rather than a randomized intervention. People who attended more sessions could differ in motivation, stability, medication-taking behavior or other factors. The association between attendance and better urine outcomes does not isolate a causal counseling effect or validate a rule that medication should be reserved for people unlikely to attend.

How complete were the measurements?

Participants missed an average of seven of 36 possible urine screens in the modafinil group and five in the placebo group. Pill-count adherence was available only when medication packages were returned: three modafinil participants and eight placebo participants returned none. A high adherence percentage among those with count data is consequently not verified exposure for everyone randomized.

Four modafinil participants required dose reduction for anxiety or sleep complaints; medication discontinuations included an elevated-heart-rate event in that arm. The authors described treatment as generally well tolerated, but this small, selected study cannot establish safety across broader clinical populations.

What does this historical evidence support?

It supports reporting a negative overall trial with uncertain subgroup observations. It does not establish modafinil as an effective methamphetamine treatment, identify a validated responder subgroup or address driving impairment. A urine endpoint measures the study’s drug-use outcome, not an individual’s functional state at a particular time.

Source

Heinzerling KG et al. Randomized, double-blind, placebo-controlled trial of modafinil for the treatment of methamphetamine dependence. Drug and Alcohol Dependence. 2010;109:20–29. doi:10.1016/j.drugalcdep.2009.11.023. Historical controlled human evidence.

Blank specimens and fortified controls can miss an interference present only in authentic samples. Toennes and colleagues discovered such a problem while developing a serum LC–MS/MS cannabinoid method. Their study shows why selectivity must be demonstrated in real specimens, while providing no basis to assume that every postmortem cannabinoid result is wrong.

This was serum-method research, not an autopsy cohort

The investigators studied THC, 11-hydroxy-THC and THCCOOH in human serum. During method development, authentic cannabis-user specimens showed a shoulder on the THCCOOH chromatographic peak that was absent from blank and fortified specimens.

The extraction used 0.2 mL serum, internal standards and solid-phase extraction before LC–MS/MS. The paper did not examine decomposed autopsy whole blood or define anatomical collection sites and postmortem intervals. Its relevance to postmortem work is the analytical question of selectivity; it does not supply direct estimates of interference frequency in autopsy specimens.

Two monitored transitions did not eliminate the interference

The unknown compound shared the THCCOOH precursor mass and both monitored fragment transitions, but had different relative fragment intensities. The investigators could not establish selective transitions that distinguished the two compounds on their own.

With an extended chromatographic program, THCCOOH eluted at 5.11 minutes and the interfering compound at 5.63 minutes. Separation allowed examination of each peak. The authors proposed structural similarity to THCCOOH, possibly an isomer, but had not established the compound’s exact structure or origin. It should not be retrospectively given a definitive chemical identity on this paper alone.

The reported percentages were estimates with a specific denominator

Of 98 forensic samples analyzed, 93 were evaluated after excluding four with no detected cannabinoids or interference and one with THCCOOH below quantification. Twenty more were excluded from the relative-concentration evaluation because the low interfering signal could not be integrated adequately.

In the remaining 73, estimated interference-to-THCCOOH concentration ratios ranged from 4.5% to 51.0%, with a median of 14.6%. The estimation used THCCOOH calibration and summed fragment responses, not a pure reference standard for the unknown compound. These percentages therefore are not demonstrated correction factors for unrelated laboratory results.

The estimated concentrations were strongly associated with THCCOOH (Spearman coefficient 0.883, P < 0.001). Association with cannabis-positive specimens did not resolve whether the compound was a metabolite or another related substance.

Method optimization addressed the observed problem

The final optimized method separated the interference while retaining a short analytical cycle. Reported quantification limits were 0.3 μg/L for THC, 0.2 μg/L for 11-hydroxy-THC and 0.6 μg/L for THCCOOH. Calibration extended to 50 μg/L for the first two and 150 μg/L for THCCOOH.

Reported recovery exceeded 95%; within-day and between-day precision was below 11%, and bias below 5%. Comparison of THCCOOH measurements using the optimized and extended methods in 93 samples showed mean deviation of 0.01% and relative standard deviation of 2.6%. Thus the study documented an identified problem and an effective response, rather than failure of LC–MS/MS as a technology.

What to examine in a postmortem laboratory record

Ask whether the actual method separates relevant interferents, how retention times and ion ratios were evaluated, and whether authentic specimens of the relevant matrix were included in validation. A clean fortified control cannot by itself establish selectivity in every real specimen.

An interference can affect identification or quantitation without being postmortem redistribution. Conversely, valid chemical measurement does not establish impairment, time of use or cause of death. See unquantifiable postmortem THC results for a different study in which authentic autopsy matrices directly limited reporting.

Primary source

Toennes SW, Hanisch S, Pogoda W, Wunder C, Paulke A. Pitfall in cannabinoid analysis—detection of a previously unrecognized interfering compound in human serum. Analytical and Bioanalytical Chemistry. 2015;407:463–470. doi:10.1007/s00216-014-8301-y.

A narrow confidence interval for a vitreous-to-blood ethanol regression slope does not mean that blood ethanol can be predicted precisely for one person. Pounder and Kuroda demonstrated this distinction in 345 autopsies: the fitted relationship was statistically well defined, but individual prediction intervals remained wide.

How the dataset was assembled

The investigators retrieved 349 medicolegal cases with paired vitreous and blood ethanol measurements from July 1988 through December 1992. Blood was typically, but not universally, femoral. Vitreous was obtained by direct needle puncture. Blood tubes contained potassium fluoride and potassium oxalate; vitreous did not. Samples were held at 4°C and analyzed within one week.

Headspace GC–FID measurements were performed in duplicate, and their means entered the analysis. The article describes the instrument and operating conditions but does not supply a complete numerical validation dataset for analytical limits, precision and recovery. Case-specific death-to-collection intervals were not provided.

Outlier review changed the final sample

Eight cases initially lay outside the 95% prediction interval, all with blood ethanol above vitreous. Four trauma cases were excluded because blood contamination was considered probable. The other four, considered potentially associated with death during absorption, remained in the final 345-case model.

This distinction matters: 345 was the fitted dataset, while 349 was the retrieved series. The exclusions were interpretive decisions after record review, not direct experimental proof of contamination. The model should not be transferred without qualification to a new specimen already suspected of contamination.

A precise slope and a wide prediction can coexist

The fitted equation was blood ethanol = 3.03 + 0.852 × vitreous ethanol, with concentrations expressed in mg%, meaning mg/100 mL. The slope’s standard error was 0.0098 and its 95% confidence interval 0.833–0.871. The intercept’s confidence interval, −1.57 to 7.63, included zero.

Those intervals concern the fitted relationship. They do not describe the scatter of individual blood concentrations around it. Table 2 makes the practical difference explicit: vitreous ethanol of 90 mg/100 mL gave a predicted mean blood concentration of 80 mg/100 mL, but a 95% individual prediction interval of 29–131 mg/100 mL and a 99% interval of 13–147 mg/100 mL.

At vitreous 150 mg/100 mL, the predicted mean was 131 mg/100 mL, with a 95% prediction interval of 80–182 mg/100 mL. Reporting only 131 would omit the much wider uncertainty relevant to an individual.

What the statistical limits assume

The prediction intervals belong to this fitted model and its sampling population. They are not guarantees for every decomposed, contaminated or differently collected specimen. Residual normality testing detected departures from normality; the authors considered the departure small enough for their analysis. That judgment should remain part of the interpretation.

The researchers also reanalyzed raw data from seven previous publications and found that equations were often different. Their central conclusion was that individual prediction uncertainty, rather than merely the precision of a conversion factor, limits quantitative usefulness.

Corroboration and reconstruction are different tasks

Paired vitreous testing can help examine an already measured blood result. Predicting a missing blood concentration requires an additional model and its individual prediction interval. Neither procedure independently reconstructs the concentration at an earlier driving event or proves the origin of ethanol.

This study did not establish impairment or cause of death from vitreous alone. Our discussion of individual blood–vitreous disagreement addresses the separate observation that either matrix can have the higher result; the present study explains how uncertainty must accompany a numerical prediction.

Primary source

Pounder DJ, Kuroda N. Vitreous alcohol is of limited value in predicting blood alcohol. Forensic Science International. 1994;65:73–80. doi:10.1016/0379-0738(94)90262-3.

A study conducted in a warm climate does not automatically validate ethanol interpretation in advanced decomposition or unrefrigerated specimens. De Martinis and colleagues compared five specimen types in Brazil, but the 21 selected cases were sampled only 3–8 hours after death, had minimal decomposition and were refrigerated before analysis. Those conditions define the reach of the findings.

The study population was narrower than its setting

Investigators collected specimens in 103 autopsy cases at the Legal Medicine Center in Ribeirão Preto, Brazil, during May–December 2003. Twenty-one cases were selected for analysis because vitreous ethanol reached at least 0.1 g/L. Eight were classified as natural deaths and 13 as violent deaths.

The average sampling interval was six hours after death. Selecting on vitreous positivity means this was not an unbiased evaluation of all possible blood–vitreous combinations, particularly blood-positive cases with little or no vitreous ethanol. It also was not a study following bodies through progressively advanced decay.

Specimens were collected and handled under stated conditions

Femoral and subclavian blood, urine and right-eye vitreous were collected before the autopsy examination began; heart blood was collected separately during the examination. Peripheral blood was obtained by external percutaneous puncture into tubes containing EDTA and sodium fluoride. Urine was obtained by puncture toward the bladder, and approximately 2 mL vitreous was collected into an unpreserved tube.

The same person collected all specimens for each case, and specimens from that case were analyzed simultaneously. They were refrigerated at 4°C for two days before analysis. The study therefore cannot be described as testing the effects of long transport without refrigeration merely because the authors discussed that practical concern.

What the comparisons actually found

Ethanol was measured in duplicate by headspace gas chromatography with flame-ionization detection, using isobutanol as internal standard. The paper describes the preparation and instrumental conditions but does not provide a complete numerical method-validation dataset for detection limits, quantification limits, recovery and imprecision.

The authors reported no significant differences among blood collection sites and described strong correlations between specimen types. Table 3 gives vitreous correlations of 0.93 with heart blood, 0.98 with subclavian blood, 0.96 with femoral blood and 0.98 with urine; the reported correlation tests were significant at P < 0.05.

The abstract gives somewhat different correlation coefficients. Those values should not be silently combined or treated as identical. More fundamentally, a significant correlation tests association; it does not demonstrate individual interchangeability or identify how much ethanol was formed after death.

Why climate is not the experimental variable

The authors discussed local temperatures and the practical importance of alternative specimens in warm settings. They did not randomly allocate specimens to different temperatures, compare refrigerated with unrefrigerated transport, or measure microbial ethanol production over time. No temperature-specific production rate follows from the results.

The reported nonsignificant site differences also do not establish equivalence for every case. This small selected series and its early sampling window cannot settle what happens after several days of decomposition, extensive trauma or uncertain storage. The authors themselves called for larger studies and longer intervals after death.

Use the actual conditions when comparing a case

When a study is offered to support interpretation of a decomposed specimen, compare the interval, preservation and handling rather than its country alone. Ask whether the research measured specimen agreement, chemical stability or actual microbial formation; these are different questions.

The study supports useful early postmortem comparisons under its stated conditions. It does not establish impairment, a fatal ethanol concentration or the fraction attributable to drinking in an individual. For experimental evidence that directly tested tissue decomposition stages, see decomposition stage and ethanol formation.

Primary source

De Martinis BS, de Paula CMC, Braga A, Moreira HT, Martin CCS. Alcohol distribution in different postmortem body fluids. Human & Experimental Toxicology. 2006;25:93–97. doi:10.1191/0960327106ht596oa.

Measuring THC in postmortem brain tissue does not, by itself, establish impairment before death. Meneses and Hernandez analyzed blood and brain specimens in 43 selected cases and found no clear distribution pattern that could translate a chemical concentration into a behavioral conclusion. Brain testing added useful analytical information, with substantial sampling and interpretation limits.

Selection and specimen availability shaped the study

The study included 21 fatally injured drivers and 22 people who were not driving at death. Overall there were seven females and 36 males, aged 17–76 years. Selection required THC confirmation in central blood and availability of peripheral blood and/or brain. This design could not measure how frequently brain contained THC when central blood was negative.

Brain was unavailable in cases receiving only an external examination. For analysis, portions from the supplied brain specimen were homogenized 1:1 by weight with water. The original anatomical regions, lobes and proportions of white and grey matter were unspecified. These measurements therefore were not standardized samples from one defined brain region.

Blood and brain did not maintain a fixed relationship

Table 2 reports quantifiable brain THC in 14 driver cases, ranging from 1.5 to 343.7 ng/g, and 17 non-driver cases, ranging from 1.4 to 50.2 ng/g. These are smaller specimen-specific counts within the total of 43 people.

The authors reported no correlation between blood and brain THC concentrations and no discernible overall distribution pattern. Their comparisons sometimes found a numerically higher brain concentration, sometimes a higher blood concentration. Blood was expressed in ng/mL and brain in ng/g; these are different matrix units, not directly interchangeable measurements.

The active metabolite 11-OH-THC was also measured. In the driver group, the authors observed higher brain than blood concentrations in the available comparisons. That finding did not establish an impairment threshold, and they considered possible information about recency of use a question for further research.

Collection and storage complicate the comparison

Central blood came from the heart-cavity area. The methods describe peripheral collection from femoral or clavicle arteries, but the exact site was not recorded on individual specimens. External examinations used blind collection. It would be inaccurate to relabel all peripheral results as anatomically verified femoral venous blood.

Blood was preserved with sodium fluoride and potassium oxalate. Central blood was refrigerated at 2–4°C after receipt; peripheral blood and tissue were frozen at −20°C. The overall postmortem interval averaged three days, with a median of two and a range of 0–27 days. All but one case were within seven days. Differing collection and storage conditions prevent assigning every blood–brain difference to redistribution alone.

What the analytical method demonstrated

Supported liquid extraction and LC–MS/MS were used for brain cannabinoids, with two monitored transitions per compound. The stated quantitative range for THC, 11-OH-THC, CBN and CBD was 1–100 ng/mL, with detection and quantification limits administratively set at 1 ng/mL. For THCCOOH the corresponding figures were 5–500 ng/mL and 5 ng/mL. Brain results were reported per gram after preparation.

The paper states that blood and brain methods had been validated, but does not reproduce all numerical validation results. Homogenized liver failed reproducibility requirements for bias and precision during validation and was excluded. A method working in one tissue did not automatically work in another.

From tissue detection to an opinion

The study lacked behavior and performance information needed to determine impairment, and cannabis dose, route and use history were unknown. The non-driver group was not a matched population of unimpaired drivers. The data therefore cannot establish crash risk or a brain concentration causing a particular driving error.

Brain can be a supplemental specimen when blood is limited, but its interpretation must retain the sampling and method limits. Compare the separate issue of central-to-peripheral blood ratios; neither type of comparison directly measures behavior before death.

Primary source

Meneses V, Hernandez M. Cannabinoid distribution in postmortem samples. Forensic Chemistry. 2021;23:100303. doi:10.1016/j.forc.2020.100303.