A new imaging study reports an acute cerebellar-dominant response to mescaline unlike the spatial patterns previously reported under LSD or psilocybin. The acute activation pattern may well be distinctive. The abstract is less careful about separating that result from cerebellar hyperconnectivity, which the same laboratory had already reported under both of those drugs. What began as a look at one overstated sentence turned into something more interesting: an education in how the regions of a brain get counted in the first place.

This started with a social media post. A striking summary, a good headline, a finding that sounded like it mattered. I went to check one sentence and came out the other side having learned something I had never once thought to wonder about, which is how anybody decides what counts as a region of a brain.

Some background first. Mescaline has probably remained the least-imaged classical psychedelic partly because of its Schedule I status and partly because it attracted less modern clinical and commercial investment than psilocybin or LSD. Until this year the entire human neuroimaging literature on the compound consisted of one SPECT study, Hermle and colleagues, twelve volunteers, 1992, reporting increased right frontal blood flow with decreases to the right thalamus and superior-temporal cortex.

That gap has now been partially filled, from an unexpected direction. Cavallaro and colleagues at Northeastern's Center for Translational Neuroimaging have published the first comprehensive pharmacological and resting-state fMRI characterisation of mescaline, in awake rats. Their discussion claims the compound produces "a unique cerebellar-selective activation pattern fundamentally different" from the cortical and thalamic effects reported for LSD and the cortico-striato-thalamic activation seen with psilocybin.

The observation looks real, and the acute pattern may genuinely be distinctive. What is harder to assess is how much of the packaged claim that pattern can carry, because the direct imaging comparison rests principally on three preceding studies from the same laboratory rather than on independent head-to-head datasets. Same magnet, same restraint apparatus, the same proprietary atlas family, substantially the same author list. Mescaline is the fourth compound through a single pipeline.

Reading all four changes what the mescaline paper is. To the authors' credit, their introduction is explicit that they expected the connectivity increase and located the distinctiveness elsewhere. Their abstract is not. One component was already established in the laboratory's own LSD and psilocybin papers, and was explicitly grouped with mescaline in a paper published thirteen days before this one was accepted.

That is the narrow version of the criticism, and it is the one that survives. Getting to it took four rewrites and a lot of things I had wrong along the way, including most of what I originally thought about the atlas. That part turned out to be the most interesting section in the piece, and not for the reason I expected.

The programme

Four compounds, one laboratory, three years.

Ghaw et al., 2024, LSD, awake rats, Brain Communications. First awake rodent fMRI study of the compound. Funded by Ekam Imaging Inc. Atlas: 173 regions.

Fuini et al., 2025, psilocybin, awake rats, Frontiers in Neuroscience. Noah Cavallaro is an author.

Cavallaro et al., 2026a, 5-MeO-DMT, awake rats, Neuropharmacology. Accepted 17 February 2026, online 6 March 2026. Cavallaro first author, Ferris senior.

Cavallaro et al., 2026b, mescaline, awake rats, Neuroscience Bulletin. The paper under discussion. Received 1 November 2025, accepted 19 March 2026, published online 21 May 2026. Cites Ghaw and Fuini as its comparators. Does not cite 5-MeO-DMT.

Each is presented as a first: the first awake LSD imaging, the first awake psilocybin imaging, the first fMRI characterisation of 5-MeO-DMT in any species, the first comprehensive characterisation of mescaline. Each is, so far as I can establish, accurate on that narrow point. The programme is a real capability and the awake preparation is a genuine methodological advance over anaesthetised rodent imaging, which is the field's standing problem.

Ferris has described the approach candidly. The laboratory works systematically through compound classes, it went through a cannabis phase, he told a Northeastern press writer in July, and published a number of studies from it. That is an honest account of an imaging platform doing what such platforms are for, and a legitimate way to run a laboratory. It is worth stating in his words rather than mine, because the serial structure is the condition under which the novelty claim has to be read, and the authors do not dispute it.

A shared platform cuts both ways here, and the piece should say so plainly. It improves comparability by reducing methodological heterogeneity between compounds, which is a real strength, and a randomised head-to-head study elsewhere would be harder to fund and slower to run. But these were separate cohorts and separate experiments, with different doses, different timing schemes, different sexes analysed differently, and differing reported atlas totals. They do not amount to a randomised head-to-head comparison. A shared pipeline also permits shared systematic bias. Persistent atlas, registration or restraint-related effects could recur across the programme, even if they interact differently with each compound and cohort. The internal comparisons may still be informative, but they require independent replication before being treated as properties of the drugs rather than of this particular preparation.

What the mescaline paper found

Twenty-four Sprague-Dawley rats, equal sexes, acclimated over five days to head restraint, given 50 mg/kg mescaline or vehicle while fully awake in a 7T magnet. Three protocols in sequence: pharmacological MRI across a five-minute baseline and twenty minutes post-injection, resting-state functional connectivity roughly ten minutes later, and an odour-provocation paradigm using almond as an innate reward. A separate cohort of sixteen ran prepulse inhibition.

The acute BOLD result is anatomically stark. Of 169 atlas-defined regions, 26 showed significant reductions in positive BOLD volume of activation and 33 showed significant increases in negative BOLD, and the tables are dominated by the cerebellum. First through tenth lobules. Crus 1 and Crus 2 of the ansiform lobule. Paramedian lobule, copula of the pyramis, flocculus, simple lobule, the fastigial and interposed nuclei. Around them, the vestibular nucleus, the inferior and superior colliculi, the cochlear nucleus, substantia nigra reticularis. Effect sizes are large, omega-squared above 0.5 for several regions.

The selectivity claim needs splitting by measure, and the distinction matters. The positive activation-volume effect is strongly cerebellar-selective: olfactory bulbs, prefrontal cortex, accumbens, thalamus, somatosensory and visual/auditory cortices all show no significant change. The negative activation-volume result is cerebellar-dominant but not exclusively cerebellar, significant changes extend into striatal, septal and hippocampal structures, with dorsal dentate gyrus, dorsal subiculum, lateral and medial septal nuclei and dorsal medial striatum all appearing in the tables. "Cerebellar-selective suppression" is accurate for one of the two measures. The authors do demonstrate that the positive-BOLD sparing is an absence of difference rather than an absence of signal: their Figure 2B shows comparable voxel counts for vehicle and mescaline at the prefrontal level, with the two conditions diverging dramatically only at the cerebellum.

The resting-state analysis then inverts the picture, and here the terminology needs care. These are thresholded functional-correlation edges, not newly grown anatomical connections. At the study's correlation threshold, numerous additional edges involving the deep cerebellar nuclei appeared under mescaline, linking them to thalamus, midbrain, somatosensory cortex and hippocampus. No hippocampal–cerebellar nuclear edges survived thresholding in the vehicle network, whereas edges involving seven of nine hippocampal subdivisions did under mescaline. The mean difference in node degree for the hippocampus was 59. The primary analysis used absolute correlation values, so strongly correlated and strongly anti-correlated activity both counted toward degree; the authors report that supplementary analyses using signed correlations, global signal regression and a range of sparsity thresholds reproduced the same group differences.

From this they build a mechanism whose theoretical grounding is legitimate, even though its application to these data remains speculative. They invoke Devor's "Great Gate," in which the cerebellum, in concert with the inferior olivary complex, functions as a predictive filter distinguishing expected from unexpected sensory input, alongside Hull's review of cerebellar prediction signals. Both citations support the general predictive-filtering framework they invoke. Devor's account has the deep cerebellar nuclei supplying much of the inhibitory feedback that gates olivary responsiveness; Hull surveys prediction signals through granule cells, Purkinje cells and the cerebellar nuclei, including nuclei neurons that track the mismatch between expected and actual movement, and cerebellar output that shapes cortical processing downstream. When Cavallaro suggest their hypoactivation could reflect disruption of an internal model or a decoupling of cerebellar cortex from its nuclei, that is a reading their sources will bear.

The chain is hypothesis rather than measurement, and the authors say so, calling for direct testing in future work combining high-resolution fMRI with computational modelling. But the gap between the theory and the data deserves stating, because of what the theory is made of. Devor's gating mechanism is olivary glomeruli, GABA-A receptor subunit distribution and subthreshold membrane oscillations between 5 and 12 Hz, and Devor notes that settling its behavioural role would require intracellular recording in vivo, a significant technical challenge. Hull's evidence is complex spikes, calcium imaging of granule cell populations, and closed-loop optogenetic manipulation of the nuclei. None of that is visible in a thresholded count of activation volume. The proposal that mescaline transforms the cerebellum into what they call an untethered broadcaster of unfiltered information is a plausible reading of a BOLD pattern, offered on a measure several levels of description away from the machinery the model runs on.

And there is a passage in Devor that the mescaline paper's own BOLD-validity discussion does not reach for. Writing in 2002 about cerebellar functional imaging, Devor makes essentially the same measurement-level warning, in paraphrase: increases in the cerebellar magnetic resonance signal could reflect climbing fibres, parallel fibres or intrinsic cortical elements, and interpreting them requires a detailed model linking that signal to neuronal activity. That is the objection this piece has been making, in the source they cite for their mechanism, twenty-four years earlier.

Two components, then, bundled into one signature: acute cerebellar-dominant suppression, and cerebellar hyperconnectivity. They need to be separated, because the comparators treat them very differently, and because, as it turns out, the authors themselves separated them at the outset.

The acute finding survives

I initially assumed the acute contrast would soften on inspection. It does not.

Ghaw's LSD paper states directly that the caudal end of the brain, brainstem, cerebellum and pons, is unresponsive to high-dose LSD. LSD's acute effects were forebrain: olfactory system, prefrontal cortex, thalamus, hippocampus. The cerebellum appears in Ghaw's high-dose positive-BOLD table only as scattered entries in both directions, the fastigial nucleus and simple lobule decreased with LSD, while the interposed nucleus increased, alongside the pontine and cochlear nuclei, these three being the named exceptions to an otherwise global positive-BOLD decrease. Those scattered findings do not resemble mescaline's broad cerebellar-dominant acute profile.

So on the acute measure, within this laboratory's own data, mescaline does differ from LSD, and Cavallaro are entitled to say so.

The qualification is that "differs from LSD" is not "unique among classical psychedelics," and the other two compounds complicate it.

Fuini's psilocybin paper breaks positive volume of activation down by region and reports a significant cerebellar effect. Critically, the low 0.03 mg/kg dose produced the lowest volume of activation, significantly less than vehicle, for whole brain, prefrontal cortex, thalamus and cerebellum. That is acute cerebellar suppression under psilocybin, at one dose, in a paper Cavallaro co-authored. It is not cerebellar-selective, prefrontal cortex and thalamus moved too, and it is non-monotonic, with activation returning at 3.0 mg/kg. The mescaline claim is specifically about selectivity, so it survives. But it survives as a narrower claim than the abstract makes, and it depends on mescaline having been tested at a single dose.

Then there is 5-MeO-DMT. Cavallaro's own 5-MeO-DMT paper reports that at 1–10 minutes post-injection, negative BOLD appeared across essentially the whole brain with the exception of the posterior cerebellum, the deep cerebellar nuclei and posterior cerebellum are circled in red in their Figure 2 to mark the regions drug did not touch. The cerebellum is not merely unaffected; it is the conspicuous exception, and the authors use precisely that regional sparing as their argument that the effect is neural rather than systemic.

Set the four side by side on the acute BOLD measure:

Four acute profiles, four different cerebellar answers. These could represent genuine pharmacological differences, different drugs producing different results is what a pharmacologically sensitive measure ought to do, and treating divergence as inherently suspicious would be a mistake. The problem is narrower. Because the compounds were sampled at single or differing doses, at different positions on their pharmacokinetic curves, with different timing windows and different sex-stratification, the programme cannot yet separate drug identity from dose-and-time effects. The limitations section acknowledges the single-dose problem, but the cross-compound novelty framing does not fully incorporate it.

The connectivity component was already known to be shared

Here the case is simpler, and the laboratory has already settled it in print.

Ghaw reported cerebellar hyperconnectivity under LSD, 33 of 39 nodes versus 13 of 39 in vehicle, P < 0.0001, and the abstract calls it an unexpected finding. Fuini reported a significant dose-dependent global increase in functional connectivity under psilocybin, highlighted by hyperconnectivity to the cerebellum.

Then, in March 2026, Cavallaro's 5-MeO-DMT paper reported a global decrease in connectivity and explained that this was at odds with previous studies from the lab on LSD, psilocybin and mescaline showing dose-dependent increases in global connectivity. Note what that sentence does and does not say: 5-MeO-DMT did not produce hyperconnectivity. It went the other way. What the paper does is name mescaline, alongside LSD and psilocybin, as one of three in-house compounds that had.

The timing is tight. The 5-MeO-DMT paper appeared online 6 March 2026. The mescaline paper was accepted 19 March, thirteen days later.

In fairness to the authors, they never claimed hyperconnectivity alone was novel. The mescaline paper's introduction is explicit: "Based on our previous findings with LSD and psilocybin in awake rats, we hypothesized that mescaline would produce region-specific alterations in BOLD signal, accompanied by enhanced global functional connectivity. However, we anticipated that the specific pattern of activation would distinguish mescaline from other psychedelics." They predicted the connectivity increase as the shared, expected outcome and located the distinctiveness in the activation pattern. The discussion is consistent with this, claiming "a unique cerebellar-selective activation pattern."

The criticism is therefore subtler than a novelty grab, and it belongs to the abstract rather than the introduction. The abstract lists cerebellar-selective suppression, global hyperconnectivity, abolished olfactory reward responses and frequency-selective acoustic gating, then concludes: "These findings distinguish mescaline from LSD and psilocybin." Plural, undifferentiated. A reader of the abstract, which is all many readers and press writers will read, cannot tell that one of those four components was predicted in advance to be shared with the two comparators named in the same sentence, and had been explicitly described by these authors as shared across LSD, psilocybin and mescaline thirteen days before acceptance. The package is presented as distinguishing; only part of it plausibly does.

That is a real problem with how the result was communicated, and it is smaller than "they claimed someone else's finding as their own."

Single doses, and what the dose-response papers show

The mescaline study ran one dose. The three comparators ran dose-response designs, and two found the connectivity effect non-monotonic.

Fuini reports the cerebellum showing a U-shaped connectivity profile, with the intermediate 0.3 mg/kg dose producing the lowest node degree. Cavallaro's 5-MeO-DMT global connectivity is U-shaped too: average degree falls from 58.5 at vehicle to 48.4 at 0.1 mg/kg, a 17% drop, then returns to 58.1 at 1.0 mg/kg, essentially vehicle level. Their conclusion is that the drug has a non-linear, dose-dependent effect on network connectivity.

Non-monotonic dose-response matters here. A single-dose experiment cannot establish whether a compound-specific effect persists across the dose-response curve. It can establish an effect at the dose tested; the observed profile might persist, weaken or reverse at other mescaline doses, and one dose cannot show which. The paper's own limitations section concedes that the single dose represents one point on the dose-response curve and that other doses might reveal different patterns.

The dose citation is looser than it looks. Cavallaro cite two sources for 50 mg/kg: Páleníček et al. (2008) and Olejníková-Ladislavová et al. (2024). Neither used it. Páleníček gave 10, 20 and 100 mg/kg subcutaneously to Wistar rats. Olejníková-Ladislavová, from Páleníček's own group, used the same three doses, again subcutaneously, again in adult male Wistars. So both cited sources tested 10, 20 and 100 mg/kg in one strain, and the study interpolates 50 mg/kg in another. Páleníček also reported substantial delayed mortality at 100 mg/kg and could not exclude toxicity as a contributor to the behavioural effects at that dose. That does not establish toxicity at 50 mg/kg, and it is not enough to characterise a therapeutic index in either direction. What it does establish is that formal dose-ranging and concurrent physiological monitoring would have been worth doing.

The 5-MeO-DMT study, for comparison, enrolled 48 animals across four doses in both sexes, 44 after motion exclusions, and found females responding at 0.1 mg/kg where males did not. Its authors conclude this highlights the importance of sex-stratified analyses in future studies and in clinical trials. The mescaline study ran 24 animals with equal sexes and reports no sex-stratified analysis. Same laboratory, same year, same argument for sex-stratification, not applied.

What BOLD is, and the paper the citation trail passes through

Cavallaro deserve real credit for raising the BOLD-validity problem themselves, at length. They cite Epp et al. showing BOLD signal changes can oppose underlying oxygen metabolism in around 40% of cortical voxels. They concede they ran no concurrent respiratory or cardiac monitoring, and that mescaline produces autonomic effects, Klaiber's human data show dose-dependent increases in blood pressure and heart rate, which themselves alter cerebral blood flow. They state plainly that their vehicle control cannot distinguish direct 5-HT2A neural effects from central responses to peripheral physiological change from neurovascular coupling alterations.

Their defence is regional specificity: a purely systemic cardiovascular effect should produce uniform change, not a hindbrain-selective one. That is a reasonable argument. It is not a complete one, since it assumes uniform neurovascular coupling across a region whose vascular architecture and metabolic profile differ substantially from cortex. The paper's own framing, hypoactivation and hyperconnectivity in the same structure simultaneously, is the configuration in which a coupling artefact would be hardest to distinguish from a neural effect.

Two things sharpen this.

First, the Epp figure is directional, and Cavallaro cite only the aggregate. Broken down, discordant voxels account for 31% of significant positive BOLD but 66% of significant negative BOLD in the main contrast, and 68–78% of negative BOLD across Epp's control analyses. What this means needs stating carefully, because it is easy to overclaim. Epp found substantially greater sign discordance between negative BOLD and estimated oxygen-metabolism changes than for positive BOLD, in human cortical paradigms. That is not an error rate, it does not mean two-thirds of negative BOLD measurements are false, and the proportion does not transfer to rat cerebellum or to mescaline. What it does mean is that BOLD sign cannot be read straightforwardly as metabolic or neuronal sign, and that interpreting negative cerebellar BOLD as neural inhibition is particularly uncertain. A substantial part of the reported suppression profile lies in that direction: 33 regions showed increased negative BOLD, alongside the 26 showing reduced positive activation volume.

Second, Fuini's citation trail runs directly through the experiment that tests this in rat, for this drug class. Spain et al. (2015) administered psilocin intravenously to anaesthetised rats and measured local field potentials and cerebral blood flow concurrently in somatosensory cortex. Neuronal responses to whisker stimulation decreased while haemodynamic responses increased, opposite directions, same region, same animals. Responses to hypercapnia were unchanged, so this is not crude vasoreactivity; it is neurovascular coupling specifically. Their conclusion is that phMRI signal changes under psilocin reflect both neuronal activity and altered coupling, and that caution is required in inferring the former from the latter.

Spain also reports that, at 0.03 mg/kg, the only significant regional phMRI change was a small decrease in the cerebellum. That is prior evidence of a low-dose cerebellar BOLD decrease under a serotonergic psychedelic, from a different laboratory, in 2015, but it is psilocin rather than mescaline, intravenous rather than subcutaneous, anaesthetised rather than awake, a different pipeline, and a single small observation rather than mescaline's broad profile. It is not another instance of the same signature. It is a reason the signature should not have been described as unreported. Fuini cite Spain. Cavallaro's BOLD-validity discussion does not.

Where the humans are

Klaiber et al. (2024) is the strongest modern human dataset on mescaline: sixteen healthy subjects, double-blind, placebo-controlled crossover, four doses from 100 to 800 mg, plus an 800 mg arm co-administered with the 5-HT2A antagonist ketanserin. Dose-dependent subjective effects above 100 mg with no clear plateau by 800 mg. Plasma half-life around 3.5 hours. Effect duration rising from 6.4 to 14 hours across the range. Ketanserin reduced the 800 mg response to roughly the level of the 100 and 200 mg doses, providing strong evidence that 5-HT2A signalling mediates most of the acute psychedelic response, as for LSD and psilocybin.

The qualitative comparison belongs to Ley et al. 2023, same group, 32 participants receiving mescaline, LSD and psilocybin at psychoactive-equivalent doses, which found acute subjective effects of 500 mg mescaline, 100 µg LSD and 20 mg psilocybin comparable across various psychometric scales, with only modest autonomic differences.

So the human phenomenology says mescaline is a classical psychedelic with unusual pharmacokinetics: slow to absorb, long to peak, hence long-acting, and commonly associated with nausea. The rat imaging says mescaline is anatomically distinctive. These are not incompatible, mechanism and phenomenology need not track, but the imaging paper's clinical speculations run ahead of where they connect. The suggestion that cerebellar targeting might have applications in movement disorders, cognitive impairments, or conditions involving sensory filtering deficits, or that frequency-selective gating might apply to auditory processing disorders, derives from a single dose in one species at one timepoint, on a measure the same paper spends two pages qualifying.

The Hermle discrepancy is left unresolved. Hyperfrontal in humans; little positive activation-volume difference in the rat forebrain. The paper offers species differences, methodological variation, or the superior resolution of awake BOLD fMRI over SPECT, three candidate explanations for one contradiction, which is not an argument for any of them.

The visual result deserves less weight than it might seem to carry. In the odour-provocation analysis, mescaline blunted BOLD responses in olfactory, somatosensory and auditory systems, while the visual system showed no significant treatment difference. In humans, visual distortion is mescaline's signature. But this was an almond-odour challenge, not a systematic test of visual processing, and the absence of a visual-region treatment difference during an olfactory task provides little direct evidence about mescaline's human visual phenomenology either way. It is worth noting that a model built to explain perceptual alteration through cerebellar sensory flooding did not produce a visual signal in the one paradigm where it was incidentally observable, and worth not building much on it.

The residue of a shared spine

Two small things, individually trivial, which together indicate how closely these papers share a template.

The mescaline paper's Degree Centrality section describes importing connectivity matrices "for both psilocybin and vehicle data." This is a two-group mescaline study with no psilocybin in it.

The paragraph is shared across all four papers, and it is worth setting out what actually happened, because the obvious inference is the wrong one. Ghaw reads "for both LSD and Veh data." Fuini reads "for both PSI and vehicle data." Both correct. The 5-MeO-DMT paper, same first author, three weeks earlier, reads "for both drug and vehicle data," having generalised the phrase so that it could not break again. Then the mescaline paper reverts to a named compound and names the wrong one. Three of four are right, and the fix was already in place. This is not a lab carelessly copying itself; it is a template being maintained competently, with one instance slipping through.

The second is narrower. The mescaline paper's connectivity methods refer to computing correlations "within all three groups." That sentence appears only in Ghaw and in the mescaline paper, Fuini and the 5-MeO-DMT study do not have it, and in Ghaw it was correct, because Ghaw had three groups.

Neither makes the underlying measurements less independent. Different animals exposed to different drugs remain independent experimental observations regardless of how the methods section was assembled. What they show is inadequate proofreading and close pipeline continuity, in a section of the paper that almost nobody reads and reviewers routinely skim. The real requirement for the argument being made, this compound differs from those compounds, is not textual independence but harmonised measurement: regional definitions, doses and timing that can be matched across studies. Which raises a question about the atlas.

The commercial arrangement belongs here too, stated plainly rather than insinuated. The senior author and imaging lead hold interests in the companies supplying the equipment: Ekam Imaging for the RF electronics and restraint hardware, Ekam Solutions for the atlas and its EVA registration software. Ghaw was funded by Ekam Imaging directly. Ferris's own 2022 review discloses a financial interest in Animal Imaging Research for the RF electronics as well, and older papers cite Insight NeuroImaging Systems for the same restrainer. Published disclosures and methods sections name several related or successive suppliers without explaining the corporate relationship among them. All of the interests are disclosed, every time.

Instrumentation markets in animal neuroimaging are small, and the people who know enough to build the tools are usually the people using them. The arrangement is unremarkable. What matters is the consequence rather than the motive: tools normally get stress-tested by outside users who hit problems and complain, and a concentrated user base reduces how much of that correction is visible from outside.

The hardware, at least, is not a lock-in. The Ekam design is a quadrature transmit/receive volume coil built into a non-invasive head restrainer, and it is good engineering, but Stenroos and colleagues built a 3D-printed restraint kit compatible with standard Bruker coils in 2018, and in 2026 eNeuro published an open-source restraint system outright. Those authors are blunt about why awake rodent imaging has not spread: procedural complexity, absent standardised protocols, and reliance on custom hardware. Nothing technically ties the atlas to the coils either, since a parcellation is a file and will take data from any scanner. Whatever keeps them together, it is not a technical constraint.

The map, and a thing that looked like a problem

Every number in this paper depends on something most readers never think about, and I had not thought about it either until I went looking.

The brain does not come with lines on it. There is no visible boundary where the thalamus ends and the next structure begins, because it is continuous tissue. So someone has to decide where the borders go, and an atlas is that decision written down: a reference brain with regions drawn on and labelled, packaged as a file. Scan an animal, warp its brain until it lines up with the reference, and every voxel inherits a label. That is how "26 of 169 regions" comes into existence. It is not a theory-free count supplied by the brain itself. It is a measurement made after continuous anatomy has been partitioned according to somebody's model of it. The regions usually have real anatomical foundations. The exact boundaries and the granularity are choices.

The atlas here is a commercial product from Ekam Solutions, the company Ferris and Kulkarni part-own. It is Paxinos-and-Watson-derived in its naming but MRI-native in its boundaries, built from 85-micron T2-weighted scans on a Bruker 7T, and the group's own methods paper says it was developed to overcome the shortcomings of existing commercial and public-domain atlases, with the reasonable argument that an MRI-based template avoids the tissue shrinkage histology introduces. Its computational framework originated in Kulkarni's doctoral work, before Ekam existed as a company.

Now look at the region counts reported across the literature that uses it:

Year Regions Source
2016 171 fragile X study
2018 173 QUTE-CE vascular paper
2020 171 diabetes study
2023 174 Ekam product page
2024 173 Ghaw, LSD
2026 169 mescaline

I want to be careful here, because my first pass at this was wrong in a way worth describing. I had also included a 2015 concussion paper reporting 150 areas, and treated the whole sequence as a version history. It is not. That paper says plainly that the atlas has 173 annotated areas and that 150 were selected for diffusion analysis, white matter tracts excluded because they traverse several regions, along with circumventricular organs and areas without clear regional organisation. That is deliberate subset selection for a specific analysis, not a different atlas. Once you notice that one, you have to assume others in the table might be subsets too, and the papers rarely say.

So what the table actually shows is inconsistent reported totals, not a documented revision history. Some of the variation is probably genuine revision. Some is probably analytical subsetting. Some could be publication error. No paper cites a version number, so there is no way to tell which is which. Ghaw says "a 3D Rat Brain Atlas©, which included 173 segmented and annotated brain regions." The mescaline paper says the atlas "parcellates the brain into 169 discrete, annotated regions." That is the entire documentation in both cases. The current Ekam product page advertises 174.

One likely contributor to the variation is inconsistent treatment of white matter, and there is direct in-house evidence for how large that effect can be. A Northeastern doctoral thesis from this laboratory is reported to describe the atlas at the start of that work as 173 annotated regions on a high-resolution structural MRI template spanning 64 serial coronal slices, with white matter represented in a single aggregated placeholder region carrying no delineations. Its stated aim was to extend that atlas with 27 individually segmented white matter tracts, yielding a 199-region atlas. So delineating white matter moves the total by twenty-six regions in one step, and 199 is a number no published paper reports. The 2015 concussion analysis moved in the opposite direction, excluding white matter tracts outright to reach 150. Between an aggregated placeholder, a 199-region extension and analyses that drop white matter altogether, closely related versions or analytical selections from the atlas could plausibly yield several different totals without every difference representing a substantive anatomical revision. Template geometry appears to have shifted too: the vascular paper describes 65 axial slices, the thesis 64 coronal. What the publications do not contain is enough information to reconstruct which of these accounts for which reported number.

Here is why this looked, for a while, like it might sink the whole comparison.

The mescaline finding is a claim about which cerebellar structures appear in the significant tables, set against Ghaw's LSD tables. If the difference between 173 and 169 had touched the cerebellum, splitting a lobule or merging the fastigial and interposed nuclei or dropping a vermis subdivision, then the two papers would be counting different things while presenting the comparison as like for like. The central result would be resting on a moved goalpost and no reader could tell.

So I checked the region names in both sets of tables.

Region Ghaw (173) Mescaline (169)
Paramedian lobule "Paramedian lobule" "Paramedian lobule"
Simple lobule "Simple lobule cerebellum" "Simple lobule cerebellum"
Fastigial nucleus "Medial cerebellar n. fastigial" "Fastigial n. cerebellum"
Interposed nucleus "Interposed n." "Interposed n. cerebellum"

Same structures, same nomenclature, differences confined to label strings. And the mescaline paper's full cerebellar inventory, first through tenth lobules, Crus 1 and Crus 2 of the ansiform lobule, copula of the pyramis, flocculus, paramedian and simple lobules, plus the fastigial, interposed and dentate nuclei, is a complete and conventional Paxinos-derived set. Nothing appears split, merged or omitted.

What that establishes is narrower than I first wrote. The named cerebellar regions on which the acute comparison depends are represented in both papers, so the region-count difference does not appear to undermine that particular comparison. It does not prove no cerebellar label changed anywhere in the atlas, and it does not compare the underlying masks. Two regions can keep the same name while their boundaries move. Without the label files or a changelog, the geometry cannot be checked from the papers at all. What the published labels show is no obvious cerebellar split, merger or omission capable of explaining the acute contrast. That is reassuring rather than conclusive, and it is as far as an outside reader can get.

Three smaller things remain, and they are all much less dramatic than what I went looking for.

The reported totals differ, so any whole-brain proportion compared across these papers, N out of 169 against N out of 173, is not quite comparing like with like. Probably minor in numerical terms, four regions out of roughly 170, but impossible to quantify without knowing which regions changed.

No paper cites a version, so the check I just ran is the only route by which anyone outside the laboratory could establish that the cerebellar labels held. And it worked only because both papers happened to publish full region-by-region tables. Had either reported summary statistics instead, the question would have been permanently unanswerable from outside.

And the visible published use of this atlas appears heavily concentrated in work involving Ferris, Kulkarni or their centre. I found no clearly independent published validation, though a literature search cannot establish that no outside users exist, and industrial or unpublished use would not show up. Compare Waxholm Space, the main open rat atlas, distributed as NIfTI with a label file, whose version 4 documents 222 structures of which 112 are new and 57 revised, with the criteria behind the annotations set out explicitly. Versioning and changelogs are demonstrably possible. A concentrated user base reduces the visible external correction that builds up around widely adopted open tools, and the publications provide little evidence of independent validation or public version tracking.

That is the honest shape of it. A proprietary tool with inconsistent reported totals and no visible version trail, in a field where that is common rather than exceptional, which on the one question I could actually test turned out not to affect the result. Worth understanding. Not a scandal.

The comparison the field has not made

Five years ago Vejmola and colleagues at the Czech National Institute of Mental Health ran a direct comparison of four psychedelics in freely moving rats, psilocin, LSD, mescaline at 100 mg/kg, and DOB, with fourteen cortical EEG electrodes and behaviour scored in parallel. Their conclusion was that all four produced global broadband desynchronisation and decreased connectivity irrespective of structural family, with only modest differences between tryptamine- and phenethylamine-derived psychedelics.

That reads as a direct contradiction of the mescaline paper, and it is not one. Vejmola's cortical montage provided no direct cerebellar recording and was poorly suited to resolving cerebellar sources. The electrodes were frontal, parietal and temporal.

The inference cuts the other way from how it is usually taken. If that montage could not have detected cerebellar involvement in mescaline, it equally could not have detected it in LSD or psilocybin. Much of the cortical EEG literature was poorly equipped to assess the cerebellum directly, and the claim that a cerebellar signature is unique to mescaline is being made against a comparison set that is one laboratory deep.

The same limitation applies to the one external result usually cited against this programme, and reading it directly complicates the picture in both directions. Reinwald and colleagues are routinely summarised, including by Fuini, as having found psilocybin decreasing connectivity in rats. What they actually report is bidirectional: a widespread cortical decrease in global brain connectivity, and alongside it a well-localised hyperconnected circuit hubbed on the dorsal raphe nucleus and the hypothalamus, both showing increased strength and participation index, with the raphe reading as a newly prominent intermediate hub between subnetworks. That is not a clean opposite of the Northeastern global-increase result. It is a different shape of answer.

Two details make the comparison harder still. Reinwald's cerebellum was not merely omitted from the analysis; it was outside the acquisition. Their gray matter mask covered 44 cerebral regions, excluding cerebellum and olfactory bulb as regions not covered by the echo-planar field of view. The coverage was physically absent, which is the blindness point stated by the authors themselves rather than inferred by me.

And they used a different atlas entirely: SIGMA, an open rat template, parcellated into 44 bihemispheric regions. Set that against a proprietary atlas reporting somewhere between 169 and 174. Fuini attribute the disparity to anaesthesia and circadian phase, which is plausible and untested. Parcellation granularity is another methodological difference that could contribute, and belongs alongside anaesthesia, dose, timing, field of view, preprocessing and choice of connectivity metric on the list of possible explanations. None of them has been tested against the others.

One more thing worth noting, because it cuts against the mescaline study rather than for it. Reinwald recorded respiratory and cardiac signals at 100 Hz throughout, applied region-specific physiological noise correction, and found that psilocybin significantly altered both heart rate and respiration relative to saline. That is precisely the monitoring the mescaline study did not do, in the paper cited as the disagreeing result.

Fuini are notably careful in a way the mescaline paper is not, they call their own result unprecedented and at odds with much of the preclinical and clinical literature, and spend a page on restraint stress, circadian timing and species differences. The most rigorous scepticism about this programme's central finding comes from inside the programme.

One further gap: unlike Fuini's study, the mescaline experiment did not attempt pharmacokinetic confirmation of plasma or brain exposure. Fuini's attempt came with its own caveat, at the low 0.03 mg/kg dose psilocin was at or below the ~5 nM detection limit, with only one of four samples yielding a measure, so the dose carrying Fuini's cerebellar suppression is not itself exposure-validated. But the mescaline study measured nothing, in a compound whose rat pharmacokinetics are known: at 20 mg/kg subcutaneously, Páleníček found serum peaking within 30 minutes and brain concentrations reaching maximum at 60 minutes, with peak brain levels about a third of serum, the molecule being polar and crossing the blood-brain barrier poorly. The phMRI window runs five minutes of baseline then twenty minutes post-injection. The acute cerebellar suppression is measured across the ascending limb, before brain concentration maximum.

What is actually on the table

Strip the framing and something worthwhile remains.

Mescaline has now been imaged whole-brain in an awake preparation, and the largest signal sits in a structure that has remained peripheral to the dominant cortical and thalamic narratives of psychedelic neuroimaging. Whether or not it proves specific to mescaline, that is a finding about where the field has been pointing its instruments. The default map, default mode network, cortical desynchronisation, thalamic gating, was drawn with priors aimed at the forebrain. Vejmola's electrodes were on the cortical surface because that is where the human EEG literature said to put them. Reinwald's field of view did not reach the cerebellum at all.

The predictive-coding story about the cerebellum as sensory gate is a decent hypothesis, properly grounded in the literature the authors cite, and they are honest that it warrants direct testing. The prepulse inhibition data are the weakest support for it. The treatment main effect did not reach significance (F = 2.97, P = 0.091), nor did the frequency effect (F = 2.48, P = 0.095); only the treatment-by-frequency interaction did (F = 3.874, P = 0.028), with ω² = 0.098, in sixteen animals across three frequencies. So the significant result is an interaction in calculated PPI, not a general enhancement of sensory gating. The abstract's headline figures, +27.6% at 4 kHz, +27.3% at 20 kHz, −16.4% at 12 kHz, are PPI percentages and should be read as the paper presents them; the separate finding that mescaline reduced startle amplitude at 4 kHz (P = 0.037) is not interchangeable with them, since PPI is calculated relative to pulse-alone response and a shifted startle baseline complicates the reading. An inverted-U across three frequencies is two intervals. It may be a real recalibration of sensory gain. It may be what three conditions look like when one of them moves.

What the study establishes is that, under this laboratory's acquisition and analysis pipeline, 50 mg/kg mescaline produced an early cerebellar-dominant alteration in thresholded BOLD activation volume in awake rats. Its positive-BOLD pattern differed clearly from the predominantly forebrain acute profile previously reported for LSD in the same preparation. The negative-BOLD result was also concentrated in cerebellum and hindbrain, though significant changes extended into septal, striatal and hippocampal regions.

What it does not establish is that every component of this profile distinguishes mescaline from classical psychedelics generally. Cerebellar hyperconnectivity had already been reported by this laboratory under LSD and psilocybin, and the laboratory's own 5-MeO-DMT paper explicitly grouped both with mescaline as compounds producing increased global connectivity, thirteen days before this paper was accepted. To the authors' credit, their introduction predicted exactly that. Their abstract does not disaggregate it. The potentially distinctive finding is narrower than the abstract implies: acute cerebellar-dominant suppression with relative positive-BOLD forebrain sparing, at this dose and this time window.

That remains an important observation. But it comes from one dose, one laboratory and one haemodynamic method, without pharmacokinetic confirmation, concurrent physiological monitoring or direct electrophysiological validation. The useful next experiment is a preregistered head-to-head comparison of mescaline, LSD and psilocybin across several doses, with harmonised timing and atlas definitions, physiological monitoring and direct neural measurement, ideally replicated on an independent imaging platform.

At present, mescaline's acute cerebellar selectivity is an intriguing result from one research programme. It is a reason to look closely, not yet a settled property of the drug.

A note on how this was checked

Earlier versions of this piece were wrong in a dozen places, and every single error made the criticism sound stronger than the evidence supported. The list is worth giving in full, because the pattern in it is the point.

I said the same laboratory had reported the connectivity finding for three other compounds; two had, and the third named mescaline in a list. I said the authors presented hyperconnectivity as what made mescaline distinctive; their introduction predicts it as shared, in plain language. I had Ghaw's cerebellar effects pointing the wrong direction. I had Páleníček supplying a dose he never administered, and missed that a second cited source did not use it either. I called negative BOLD "two-thirds unreliable," which is not what Epp established. I called Spain a third independent instance of the same finding, when it is a different drug by a different route in anaesthetised animals. I said nothing had cited the paper; citations exist. I said Reinwald had simply found decreased connectivity, when the result is bidirectional. I had the atlas drift threatening the central comparison, until checking the region labels showed them stable. I had built a seven-point atlas version history containing at least one number that was never a version at all, but a deliberately selected subset for a different analysis. And I twice thought the Great Gate model had been misapplied, first in its direction and then in its emphasis, until reading Devor and Hull showed the authors' framing is properly supported by both.

What survived was the narrower communication criticism, resting on the papers' own words and dates: the abstract lists shared and potentially distinctive findings together before concluding collectively that "these findings" distinguish mescaline, the 5-MeO-DMT sentence grouping all three compounds, the thirteen-day gap, Epp's directional split, and Devor's own warning about cerebellar BOLD. That narrower case survived the subsequent checks.

The pattern is exact and it is not flattering. Everything that died was an inference I had made about what the authors were doing. Everything that lived was either a quotation or a date.

Which is the same failure mode this piece attributes to the paper under discussion: the pull toward the version of a result that reads more strongly than the data warrants. It is not a failure of honesty. It is what happens by default, to anyone, unless something forces the check. I mention it because a critique that could not survive being checked would not deserve to be read, and because the reader is entitled to know which claims here are quotations and dates and which are my characterisations.

Sources

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Cavallaro N, Rai P, Akins D, Soltanpour S, Nasseef MT, Ortiz R, Madularu D, Kulkarni PP, Ferris CF. Beyond the toad's kiss: Mapping acute 5-MeO-DMT effects on brain connectivity across sex and dose using awake rat neuroimaging. Neuropharmacology 2026;291:110886. doi:10.1016/j.neuropharm.2026.110886

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Note on sourcing. Several technical details in the atlas section come from single in-house sources for which I found no independent corroboration, and readers should weight them accordingly.

The 85-micron acquisition, the 65-slice axial geometry, and the account of the atlas having been built to improve on existing commercial and public-domain atlases come from the QUTE-CE vascular paper and its companion data article.

The description of the atlas as 173 regions across 64 serial coronal slices, of white matter as a single aggregated placeholder region, and of the planned 199-region white matter extension come from the Northeastern doctoral thesis listed above. That repository blocks automated retrieval, so I have not inspected the full document; those details are as reported in the indexed text of the thesis, and I have written them as reported rather than as verified.

The 171-region figures in the table come from the fragile X and diabetes studies as cited; I have those from indexed excerpts rather than full-text inspection. The 150-region figure and its explanation as a deliberate analytical subset come from the minocycline head-injury paper, which states it directly. The 173 and 169 figures come from Ghaw and from the mescaline paper, both of which I read in full. The 174 figure is from the Ekam product page.

No atlas version numbers were available from any source, published or commercial.