A mechanism
Carson, S. H. (2011). Creativity and psychopathology: A shared vulnerability model. Canadian Journal of Psychiatry, 56(3), 144–153.
An audit
Schlesinger, J. (2009). Creative mythconceptions: A closer look at the evidence for the “mad genius” hypothesis. Psychology of Aesthetics, Creativity, and the Arts, 3(2), 62–72.
Two papers can both be careful, both be right about what they claim, and still leave you unable to say what you now believe.
That is what this week did to me. It took me a while to see why, because the two readings barely touch: one asks how the thing works, the other asks whether the thing is there. What made it uncomfortable is that the second one gets to go first, and I had read them in the other order.
The model
Shelley Carson’s shared vulnerability model starts from an association rather than a slogan: elevated rates of mood disorders, schizophrenia spectrum disorders and alcoholism have been reported among highly creative people.
Her proposal is not that illness produces creativity. It is that certain biological factors raise risk for both, and that the outcome depends on what capacities sit alongside them.
Vulnerability — more gets in
Reduced latent inhibition — the filter keeping irrelevant stimuli below awareness lets more through.
Novelty salience — attention pulled to the unfamiliar. Also linked to alcohol abuse.
Neural hyperconnectivity — areas linking that usually don’t.
Protective — capacity to hold it
High IQ
Working memory capacity
Cognitive flexibility
Both present → novel combinations
Vulnerability alone → being overwhelmed
What makes this a moderation model rather than a causal one is that the vulnerability has no fixed value. The same trait is an asset or a liability depending on the company it keeps. Testing work taught me the shape before psychology gave me the name for it: a system that accepts work faster than average is either your best component or your next outage, and which one it is has nothing to do with the intake rate. It depends entirely on whether the thing behind it can absorb what arrives. Carson’s proposal has that structure, and it is a considerable improvement on suffering fuels art.
Two of her points cut hard against the romantic version, and both deserve quoting rather than paraphrasing.
The inverted U, which is the anti-myth
Carson reports the inverted-U pattern from two directions. Richards and colleagues found that people with cyclothymia and the first-degree relatives of people with bipolar disorder scored higher on creativity than either non-disordered controls or the people with bipolar disorder themselves. Kinney and colleagues replicated the shape in the schizophrenia spectrum: peak creativity in people with schizotypal personality disorder or two schizotypy signs, higher than in people with no signs — and higher than in people with full schizophrenia.
The illness, at full strength, takes the work away.
Carson extends the same shape to alcoholism — as with other disorders, she writes, creative people may find that drinking inspires creativity while full-blown alcoholism is detrimental to the work.
I would flag that one, though, because it is a weaker claim than the two above it and arrives in the same sentence rhythm. The bipolar and schizotypy curves rest on Richards and Kinney measuring people. The alcohol curve rests on a biographical study of Hemingway, Poe and Fitzgerald, and on the analogy carried by as with other disorders. Three claims presented at one confidence level, standing on three different quality of evidence — which is the exact failure this article is about, occurring inside the paper I am praising.
And there is a therapeutic implication that follows directly. If creativity and psychopathology are different outcomes of shared vulnerability, then art, music and writing therapies might reduce symptoms by strengthening the protective side rather than suppressing the vulnerable one. That is a treatment idea with a mechanism attached, and it is the most useful sentence in the paper.
The audit, and the exact point of contact
Judith Schlesinger’s review, published two years earlier, goes back to the primary studies behind the mad-genius idea — principally Nancy Andreasen, Arnold Ludwig and Kay Redfield Jamison.
Here is the overlap I did not expect. Carson cites those same studies. Andreasen (1987) and Jamison (1989) appear in her introduction as the traditional empirical warrant for the association — the reason the question is worth asking — before she constructs the cognitive model.
I want to be careful here, because the tidy version of this article would overstate it. Her mechanism does not rest on those thirty interviews. It rests on experimental cognitive work: latent inhibition paradigms, schizotypy scales, working-memory tasks, imaging. If Andreasen (1987) vanished tomorrow, the mechanism would still have its own evidence to answer for. What the two readings share is narrower than a dependency — one specific number, looked at from two distances.
80%
of writers at the Iowa Writers’ Workshop had suffered a mood disorder; writers were 4× more likely than matched controls to have bipolar disorder, and 30% met criteria for alcoholism against 7% of controls (Andreasen, 1987, as cited in Carson, 2011).
The same study, opened up
writers interviewed in total, over fifteen years.
of the 30 were men, mean age 37 — and “well-known,” which most writers are not.
blinding. Andreasen conducted the interviews herself, knowing each participant’s group — what Schlesinger calls the inevitable contribution of experimenter bias at every critical juncture.
categories lumped to reach 80% — severe depression and mania together with a vague hypomanic experience “at some time in their lives.”
On Jamison (1989) her structural point is sharper still: because there was no control group, none of the results could undergo customary statistical analysis, which is why the discussion reports simple percentages. Schlesinger’s verdict across the literature is not false but unestablished — presented as definitive, never replicated, the jury still out. That was written in 2009. Hold that date — it turns out to matter a great deal.
The detail I keep is the self-selected volunteer. Recruit for a study on mood disorders and creativity, and the people who come forward are people for whom that pairing already means something. The sample gets assembled by the hypothesis — the same defect I found in a survey plan of my own, where the recruitment tactic was a dose of the variable under study.
The layer they argue on
This took me two passes, and it is the whole article.
Does the association hold?
Schlesinger’s question, about the primary studies. Her answer: not on this evidence.
By what mechanism?
Carson’s question, answered in detail. Any mechanism presupposes something to explain.
A mechanism explains how an effect would work. It cannot establish that it does.
Carson never claims otherwise. The confusion is mine as a reader — layer 2 arrives so much more specified than layer 1 that it feels like the stronger claim.
Named genes and neurotransmitter systems make a claim feel decided, when what they describe is how the claim would work if it holds. This is not a charge against Carson, who is explicit that she is proposing something to be tested. It is a description of what her paper does to me while I read it. I do a smaller version constantly: a detailed root-cause narrative — this call path, this race window, these two threads — is enormously convincing, and none of the detail establishes that the failure happened for that reason rather than a simpler one I never checked. Detail is not evidence; it is a description of what the evidence would mean if it held. I have needed a formal method to pull me back from exactly that more than once.
So layer 1 has to be settled on its own terms, by someone who goes and counts. Which is precisely what happened next.
What happened at layer 1 after 2009
Everything above stops in 2009, and I nearly let the article stop there too — which would have been its own version of not checking what a claim stands on. Schlesinger audits the small studies and finds them wanting. That is a verdict on those studies, not on the world. The obvious next question is whether anyone subsequently went and looked properly.
They did, almost immediately — and Schlesinger had told them exactly what to build. Near the end of her paper she writes that there are
no large-scale population statistics to claim, with the assurance borne of real mathematical power, that any one occupation is more vulnerable to affective disorder than any other — and little hope that there ever will be.
That is a specification. It names the study that would settle the question, and then forecloses it. Two years later the Karolinska Institutet built precisely that study, because Sweden had been quietly assembling the raw material for forty years.
30
writers — Andreasen, 1987
47
artists and writers — Jamison, 1989
300,000
patients and their unaffected relatives — Kyaga et al., 2011
1,173,763
in the 40-year follow-up — Kyaga et al., 2013
Two years after the audit, the question got asked at four orders of magnitude.
Simon Kyaga and colleagues at the Karolinska Institutet matched Swedish inpatient records against occupational data. People with bipolar disorder were overrepresented in creative occupations, and so were the undiagnosed first-degree relatives of people with bipolar disorder and schizophrenia. That second finding is the interesting one, because it is the shape Carson’s model predicts and the shape Richards found in a room of ninety people: the advantage sits beside the illness rather than inside it.
So the honest state of play is not the one my draft implied. Schlesinger was right that the 1980s studies could not carry the weight put on them, and the association she found unestablished was subsequently supported on evidence she would have had no methodological objection to — no volunteers, no unblinded interviewer, no thirty people.
The 2013 follow-up then does something I did not see coming, and it is the reason I rewrote this section. Broken down by profession, the creative group as a whole came out clean on almost everything — bipolar disorder was the only diagnosis elevated across dancers, photographers, researchers and authors alike. One occupation did not behave like the others.
Artistic and scientific professions overall — bipolar disorder only. On the rest of the diagnoses, indistinguishable from everyone else. The mad-genius story does not survive this row.
Over twice the rate of schizophrenia and of bipolar disorder against controls — plus unipolar depression, anxiety disorders, alcohol and drug abuse, and around 50% higher suicide.
Creative professions more common among relatives of people with schizophrenia, bipolar disorder and anorexia nervosa. The advantage sits beside the illness, not inside it.
Sit with that last line, because it complicates the tidy story in both directions. Andreasen’s method was everything Schlesinger says it was — thirty self-selected volunteers, no blinding, categories lumped to reach a headline. And her domain was, of all the creative occupations a national registry can count, the one that behaves differently from the rest. She generalised from writers to creative people, which the registry says you cannot do. But she was not looking in the wrong place.
The two populations are not the same population, and the mismatch runs in an awkward direction. Andreasen was studying eminent literary writers at a famous workshop. A national registry counts everyone whose occupational code says author — the copywriters, the technical writers, the translators, the person who does textbook chapters. It is a wider and much flatter net. That the signal survives being diluted that far is the part I find hard to explain away.
A study that cannot carry the weight of proof can still be pointed at a real signal. That is a more uncomfortable finding than either “she was right” or “she was wrong,” and it is the one the evidence supports. Andreasen (1987) was an exploratory clinical series of thirty people. It became a bad study at the moment two decades of citation treated it as epidemiology.
One caveat keeps me from over-correcting. Registry work substitutes occupation for creativity, which is a coarse proxy: it counts people employed as authors, not people who write well, and the two overlap imperfectly. Everything above is a claim about job titles.
Which is its own small lesson. The audit did not close the question; it raised the standard of evidence required to answer it, and someone then met that standard.
Being fair to the model
Carson’s account does not stand or fall with Andreasen and Jamison, and it would be lazy to imply it does.
Latent inhibition work, molecular genetics, and synaesthesia prevalence — reported as 7 to 8 times higher among highly creative people — sit outside the literature Schlesinger reviews.
Nettle found poets and artists high on positive schizotypy — and mathematicians lower than the general population. Replicated by Rawlings and Locarnini. “Creative people” is not one group.
The paper presents itself as a proposal that neuroscience, psychology, psychiatry and molecular biology all have a role in testing. That is the right register — and the one the popular retelling drops.
The mathematicians are my favourite detail in either paper. If the mad-genius story were true as told, it should hold across creative fields. It doesn’t — the direction reverses. That single finding does more damage to the myth than the whole audit, and it comes from the paper building the model.
And it is the same finding the Swedish registry arrives at from the opposite direction. Nettle got there with schizotypy questionnaires and a few hundred people; Kyaga got there with occupational codes and 1.17 million. Neither could have produced the other’s evidence. Both say: creative people is not one group, and every claim that treats it as one is measuring a blend.
What I take from it
Both papers, from opposite methodological positions, object to the same cultural story. Schlesinger closes by welcoming a move toward celebrating rather than pathologising people with exceptional gifts. Carson’s inverted U says the full disorder takes the work away. Neither leaves the romance standing — which matters, because if you believe suffering is the engine of good work, treatment starts to look like a threat to the work, and people delay getting help to protect something they’ve been told they’d lose.
The transferable lesson is smaller and blunter. Before admiring how well a model is built, find out what it stands on — and follow one citation back to the original method section rather than the abstract. Which is precisely what Schlesinger argues two decades of citers did not do.
What I did not expect is where that ends up. Checking the foundation does not reliably demolish the thing standing on it. Sometimes it relocates the claim: narrower than advertised, differently supported, and still there. Andreasen’s headline number was produced badly and pointed at something real. The version of this habit that only looks for reasons to discard is not rigour either — it is the same shortcut with the sign flipped.
I have never once done that for a framework I liked. I adopt the ones that match something I already believe, and from the inside, the well-founded and the unfounded feel identical. The only reason I did it this time is that someone put both papers in the same week and left them standing.
That is a harder thing to assign than either paper alone, and I am grateful for it. If you rely on a model at work: whose study is underneath it, and have you read the method section or only the summary?
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