Eight Years Later, Someone Ran It.

A follow-up to Endogenous DMT in Humans: A Critical Review of the State of the Evidence. That piece surveys the evidential structure; this one is about two results published five days apart, and what they do to it.

David Nichols' 2018 review in the Journal of Psychopharmacology is remembered as the paper that took apart the pineal-DMT hypothesis. He wrote it up from a talk he gave at Breaking Convention in Greenwich the previous year, at the suggestion of people in the audience.

The pineal demolition is not the interesting part. The interesting part is a short passage near the end, after several pages arguing that the evidence for DMT accumulating in the brain was either absent or based on flawed experiments. Nichols does not simply assert the negative. He names the experiment that would settle it: incubate radiolabelled DMT with synaptosomes taken from rats pretreated with a monoamine oxidase inhibitor, and use reserpine to block vesicular uptake. If DMT accumulates, you will see it accumulate. If it is stored in vesicles, blocking the vesicular transporter will show that too.

Then he stops. A falsifiable claim with a named test attached, which in this literature is rarer than it ought to be.

In February 2026, in Neuropharmacology, Mikael Palner and colleagues published something close to the in vivo version of that experiment. It is not Nichols' protocol. It is the question asked of a living animal rather than a tissue preparation, and the answer was a clean negative.

Five days earlier, in the Journal of Neuroscience, a group at Michigan had published a result pointing the other way.

The test

Palner's group gave rats pargyline, an irreversible MAO-A/B inhibitor, at 50 mg/kg, and looked for endogenous DMT in frontal cortex, striatum, diencephalon and cerebellar vermis ninety minutes later. The logic is Nichols': if the brain is making DMT and monoamine oxidase is destroying it as fast as it appears, then removing monoamine oxidase should let it pile up.

They found none. Endogenous DMT sat below the assay's detection limit of 0.5 ng/g in every condition and every region, pargyline included.

The control worked. The same pargyline treatment roughly trebled brain serotonin, reaching 1775 ng/g in diencephalon. The assay worked too: when the same animals were given exogenous DMT with harmine, cortical concentrations peaked around 1000 ng/g at thirty minutes and washed out almost completely by 210 minutes. The instrument could see DMT. It just could not see any that the rat had made.

They then ran the second half of Nichols' proposal, updated. Instead of reserpine they used dihydrotetrabenazine to block VMAT2, and added escitalopram to block the serotonin transporter, testing whether exogenous DMT is taken up and held in serotonin terminals as a putative co-transmitter. Escitalopram changed nothing, in any region. Dihydrotetrabenazine did not change DMT levels either, though it raised the acidic metabolite 3-IAA by around a quarter in striatum and hippocampus: a faint hint of some small vesicular pool, and the only positive signal in the paper.

Why this is a negative result and not just a null one

Failing to find something is cheap. What makes this worth reporting is that Palner did the arithmetic on what they could have found.

Given an assay limit on the order of 1 ng/g, they calculate they would have detected DMT accumulating after pargyline at a rate as low as 0.02 ng/g per minute. For comparison, in the classic work on trace amine turnover, phenylethylamine accumulated at 0.5 ng/g/min after pargyline and tryptamine at 2.4 ng/g/min. If DMT behaved like the trace amines it is usually grouped with (synthesised continuously, never stored, destroyed immediately by MAO) the experiment had something like two orders of magnitude of headroom to see it.

The comparison is not perfectly clean. The older tryptamine work used a much larger pargyline dose, 225 mg/kg against Palner's 50. But the gap is wide enough that the caveat does not close it.

Palner's own conclusion is carefully worded, and the wording matters. They say their results are not consistent with the turnover of an endogenous DMT pool in the manner of the classical trace amines. That is a narrower claim than the one the coverage has been making on their behalf. It is a claim about a pool and its turnover, not a claim that no molecule of DMT exists in the rat cortex.

Which is fortunate, because five days earlier somebody had found some.

The other paper

On 4 February 2026, Nicolas Glynos and colleagues published in the Journal of Neuroscience the study that had been circulating as a preprint since April 2024. Its main business is the neurochemical and neurophysiological effects of intravenous DMT in rats, using cerebral open-flow microperfusion to sample interstitial fluid continuously from medial prefrontal and somatosensory cortex, with simultaneous high-density EEG.

The relevant part is the baseline. Before any drug was given, in drug-naïve animals, they detected cortical DMT in 70 to 80 per cent of the rats tested, at concentrations they describe as comparable to serotonin and dopamine in the same samples.

And they did it by ultra-high-performance liquid chromatography coupled to tandem mass spectrometry, with deuterated internal standards.

That last point closes an escape route. The convenient way to dismiss the 2019 Dean microdialysis result, which found extracellular DMT in rat cortex at around 1 nM against serotonin at 2.10 nM in the same dialysates, was to note that it used HPLC with fluorescence detection, which is less specific than mass spectrometry. That objection no longer works. The observation has been repeated in different cortical regions, by a different sampling method, on a mass spectrometer.

It is not a uniform signal. In twenty to thirty per cent of animals there was nothing to find, which is itself worth explaining and nobody has.

Where the contradiction actually sits

It is tempting to line the two 2026 papers up as a straight collision: one mass-spectrometric study finds endogenous cortical DMT, another finds none. That framing is too tidy, and anyone who reads both will spot why.

They are not measuring the same quantity. Glynos sampled interstitial fluid, continuously, in awake animals. Palner extracted whole brain regions post mortem and measured tissue content. A compound present in interstitial fluid at sub-nanomolar concentrations need not produce a detectable whole-tissue pool, provided there is no pool: provided it is synthesised, released and deaminated with nothing held back. For serotonin the tissue-to-extracellular gap is two or three orders of magnitude, and the reason is vesicular storage. Take the storage away and the gap collapses. Palner's own transporter experiments found no evidence of DMT being held in serotonin terminals, which is consistent with exactly that picture.

So the two results are not, on their face, incompatible. What makes them incompatible is one specific experiment.

A compound with no storage pool, continuously synthesised and continuously destroyed by monoamine oxidase, is the textbook case of something that should accumulate when you block monoamine oxidase. That is what tryptamine does. It is what phenylethylamine does. It is the entire logic of the pargyline manipulation, and it is why Nichols proposed it.

DMT did not accumulate, at a sensitivity roughly two orders of magnitude finer than the comparable trace amines require.

The disagreement therefore narrows to something precise. Either the cortical DMT that Glynos detects is being produced too slowly to accumulate measurably across ninety minutes of MAO blockade, in which case it is present but turning over far below trace-amine rates and its functional significance is an open question; or it is not being produced at all, and something else is going on in the perfusate.

Both papers are also about contamination

There is a thread running through this that neither result is usually reported with.

Palner's group had previously reported trace endogenous DMT in rat brain, in a 2023 study with Cumming. In this paper they withdraw that reading, attributing it to contamination of the sample tray by material from animals in the same run that had been given DMT and harmine. They took specific measures this time, cleaning the dissection workstation between each brain, and the trace disappeared.

That is a small methodological confession with large implications. Endogenous DMT in mammalian tissue has always been measured at the edge of what instruments can resolve, in laboratories that also handle exogenous DMT at doses producing tissue concentrations a thousand times higher. Palner's own animals went from undetectable to 1000 ng/g in frontal cortex within half an hour of injection. How much of the historical positive literature is carryover is not a question anyone can answer retrospectively.

It is also the reason the Glynos baseline finding needs to be read carefully rather than triumphantly. Their measurement is a pre-drug epoch in animals that would shortly receive intravenous DMT, on equipment used for both. The authors did not make endogenous DMT the central claim of the paper, and were right not to.

The live question in this field is no longer analytical specificity. Two independent groups have now seen the signal on tandem mass spectrometers. The live question is carryover, and one of the two 2026 papers is a worked example of what it costs.

And the enzyme has gone missing

Underneath both positions is a problem that cuts against everybody, and it was created by the lab that has done most to argue for endogenous brain DMT.

Dean's 2019 paper made its case partly on colocalisation: INMT and AADC messenger RNA expressed in the same cells in rat visual cortex, hippocampus, pineal and choroid plexus, offering a plausible cellular mechanism for local synthesis. The paper explicitly named what would be needed to close the argument, which was INMT-deficient animals.

Four years later, Glynos and colleagues in the same group made them. Brain and lung tissue from INMT-knockout rats showed tryptamine-dependent methylation activity statistically indistinguishable from wild type. Whatever the products of that reaction are, they are not N-methyltryptamine and not DMT. Recombinant rat INMT showed no tryptamine-methylating activity under the conditions tested, while rabbit and human INMT were both robustly active. Rat INMT shares only 57 per cent sequence homology with the rabbit and human enzymes, which are 89 per cent homologous with each other.

The authors are careful about how far this goes. Enzyme behaviour is highly condition-dependent, and they explicitly expect that different assay conditions or a broader enzyme screen might yet turn up NMT and DMT production in rat tissue. Their conclusion is not that rats cannot make DMT. It is that if they do, INMT is not how, and their best guess for the unidentified products is β-carbolines formed by a Pictet-Spengler route.

This is genuinely to the Michigan group's credit. They asked for the decisive animal, built it, and published a result that removed the enzyme from their own mechanism, then went on to argue that an alternative INMT-independent pathway must exist. It also means that when Nichols spent several pages in 2018 on INMT kinetics, substrate affinities and product inhibition, he was arguing about an enzyme that, in the relevant species, is probably not doing the job either way. The 2025 Neuropharmacology review by Schimmelpfennig and Jankowiak-Siuda lands a fair hit on that section from the other direction, pointing out that the concentrations at which DMT inhibits INMT are micromolar while the concentrations at which it activates receptors are nanomolar. Both critiques survive. Neither settles anything.

What is actually at stake

Two things are worth separating out, because they are routinely conflated.

The pineal-as-major-source hypothesis is dead, and it was not Palner who killed it. Dean's 2019 paper showed that cortical extracellular DMT was no different in pinealectomised rats, which does most of the damage to the claim Nichols went to Greenwich to attack. That result was published by people arguing for endogenous brain DMT. Dean are careful to add that it remains uncertain whether the pineal contributes anything at all, so the narrower question is not formally closed. But anyone still framing this as a fight about the third eye is seven years behind.

And the therapeutic literature is untouched. In January of this year, in the Journal of Neurochemistry, Caro Aponte and colleagues reported that DMT extracted from Mimosa tenuiflora and given to rats at 1 mg/kg after ventral root avulsion raised motoneuron survival from 22 per cent to roughly two-thirds, rising to 75 per cent when combined with surgical reimplantation, with GDNF upregulated only in the combined group. Notably, the lowest dose worked best. Whether the mammalian brain makes its own DMT has no bearing on whether administered DMT protects injured neurons. Those are separate questions with separate evidence, and a negative answer to the first costs the second nothing.

What is left is narrower and more interesting than either camp's headline. There is extracellular DMT in awake rat cortex, seen twice, by two sampling methods, most recently on a tandem mass spectrometer, in most but not all animals. There is no detectable tissue pool, no accumulation under MAO blockade, and no retention in serotonin terminals. There is no identified enzyme in the species where all of the measurements are made. And there is still no demonstration that endogenous DMT does anything at the concentrations at which it has been reported.

Nichols named an experiment. Something close to it has now been run, and on the specific question he posed, whether there is a hidden pool that MAO inhibition would expose, it came back his way. That is a real result and it deserves to be treated as one rather than absorbed as another data point on a spectrum.

But it did not come back to an empty field, and the piece of it that contradicts him was published the same week.

The experiment that is now missing

The obvious next move is cheap and nobody has done it.

Give pargyline, and then sample interstitial fluid with mass-spectrometric detection in the same animals. Palner blocked monoamine oxidase and looked at tissue. Glynos looked at interstitial fluid without blocking monoamine oxidase. Neither has done both. If cortical DMT is real and turning over, MAO blockade should raise it in the perfusate, and the size of that rise is the number this whole argument has been missing.

Palner suggest a second one themselves. Give a centrally acting AADC inhibitor. If the endogenous 3-IAA they found in striatum comes from tryptamine, as they suspect, it should vanish.

Both are undergraduate-simple by the standards of the equipment already installed in these laboratories. Someone should do them.

Disclosure noted in the source: the corresponding author of the Palner paper reports consultancy work, research collaborations with several psychedelic-sector companies, and equity in Atai and Compass Pathways. The direction of interest in a negative finding about endogenous DMT is not obvious, but ARDMT's practice is to state disclosures rather than judge them.

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