Experimental History · 140 posts · opened 1 January 2022, roughly one post every two weeks ever since, unbroken for four years and eight months · latest post 15 September 2026, still active · typically 2,500–5,000 words a post · about 19% of posts are paywalled, the rest free; this page draws only on the public ones · read for this page: 14 posts spanning January 2022 to August 2026, six of them from the earliest 20% of the blog's life · selection anchored on the author's own list of his eleven most-viewed posts, plus several he keeps citing back to
Exactly one of Einstein's papers was ever peer reviewed. He was so surprised and annoyed that he pulled it and published in a different journal instead.
In late 2022 a man with a fresh Harvard PhD in psychology dug that fact up and then did the accounting. Science, he said, has spent the last sixty years running an experiment on itself. The hypothesis: have someone check every paper and reject the ones that don't pass muster, and science will be better off. There was no randomization, no control group, nobody in charge, nobody taking consistent measurements — and every scientist on Earth was enrolled.
He laid out the results. Scientists collectively spend about 15,000 years reviewing papers every year. In three studies where researchers deliberately planted major flaws in manuscripts and counted how many reviewers caught, reviewers caught 30%, 25%, and 29%. Not typos — flaws at the level of "the paper claims to be a randomized controlled trial but it isn't" and "when you look at the graphs, it's pretty clear there's no effect."
And one detail worse than any statistic: when one editor started asking authors to supply their raw data after they'd submitted, half of them withdrew the paper. In the editor's words, this suggests "a possibility that the raw data did not exist from the beginning."
The results are in. It failed.The rise and fall of peer review, 13 December 2022
The man is Adam Mastroianni, and he wasn't only complaining. A month before writing that, he had taken a paper good enough for a top journal — eight studies, over a thousand participants, preregistered, all data and code public — and published it as a blog post. It has jokes in it. In one passage he cheerfully admits he can't remember why he ran one of the studies; he asked his collaborator, who replied, "bro I do not even remember RUNNING this one." He assumed he'd look like a dummy and nobody would notice. Instead, before he'd told anyone about it, thousands of people found it, strangers emailed him thoughtful reviews, NPR asked for an interview, and it got more views than his last paper in PNAS.
But what makes the blog worth finishing isn't that he showed peer review doesn't work. It's what he did next, which was to change the frame.
There are two kinds of problems, he says. Weak-link problems, where overall quality depends on how bad the worst stuff is — food safety is one; a single bad batch of beef can kill you, so inspect the plants. Strong-link problems, where quality depends on how good the best stuff is and the bad stuff barely matters — music is one; you listen to what you love and never learn the rest exists.
His central strike: science is a strong-link problem, and we have been managing it as a weak-link problem. Phlogiston, the luminiferous ether, geocentrism, phrenology — they all died, not because a gatekeeper stopped them, but because they were useless. And weak-link gatekeeping carries a symmetrical cost that nobody bills, because it makes no sound:
The terrible study that gets published sounds like nails on a chalkboard, but the terrific study that never got funded sounds like nothing at all. Purge all the terrible at the cost of the terrific, and all you're left with is the mediocre.Science is a strong-link problem, 11 April 2023
The other half of his work is that he is a psychologist who thinks his own field hasn't yet established what it is studying. He has an image he's used for years: we're all on a bus that's supposedly going to Cincinnati, with no road signs and no GPS, so nobody knows whether we're pointed the right way. Which led him to do something few people do — instead of asking whether the field's conclusions are right, he asked how we could know we were getting closer to Cincinnati. He built five yardsticks and concluded that psychology passes exactly one of them: it is excellent at overturning folk intuitions. Meanwhile, of the 298 disorders in the DSM, zero have been cured.
His own research has the same refusal to flatter. He and a friend came up with a hypothesis over omelets, ran the studies, found they were completely wrong, and hit something stranger: ask people how something could be different, and they almost always imagine how it could be better. Fifty-two items, not one exception; 90% of participants; same result with Polish participants, same result with people in China answering in Mandarin. Asked about pets — the highest-rated item of all, rated better than "love" and "happiness" — one participant answered:
"They could be immortal."Things could be better, 15 November 2022
His other big project went at a claim head-on: everyone says morality is declining — is it? He pulled 177 US surveys (220,772 people) and 58 surveys from 59 other countries (354,120 people) and confirmed the belief is near-universal, held by old and young, liberal and conservative alike. Then he went looking for actual indicators: 107 surveys asking things like "were you treated with respect all day yesterday," 4.4 million people, 1965 to 2020 — no change at all. In one Gallup series, about 70% of people say morality is getting worse every single year, while every year people's actual answers stay the same. His proposed mechanism is BEAM: bad news gets disproportionate attention (biased exposure), and the badness of bad news fades faster than the goodness of good news (biased memory). So today always looks awful and yesterday always looks better.
The elegant part is that it predicts its own exceptions. Ask people about the individuals they personally know — where their exposure isn't negatively biased — and they say those people have gotten more moral. Ask them about years before they were born, where they can have no memories to fade, and their answers amount to saying: moral decline began when I arrived on Earth.
Notice that, while lots of people are happy to tell you about Golden Ages, nobody ever seems to think one is happening right now. Maybe that's because the only place a Golden Age can ever happen is in our memory.The illusion of moral decline, 7 June 2023
Four years in, all of it points at one temperament, which in 2026 he finally stated outright: incentives are for losers. Doing a thing because an arbitrary reward system will hand you a little treat is what pigeons do, not people. His analogy comes from the few miserable years he played Little League, where the team's shared batting helmets were rancid and ill-fitting and the serious kids brought their own.
incentives are like batting helmets: if you don't bring your own, you'll have to use the crappy ones that are provided for you.Incentives are for losers, 5 August 2026
That is the single move under all of it. Review systems, grant panels, the insistence that we must prevent bad research from being published — those are helmets somebody handed you. Every time, he takes the helmet off first and checks whether there's anyone underneath.
Exactly one of Einstein's papers was ever peer reviewed.
He was so surprised and upset that he withdrew it and published in a different journal. Requiring every paper to clear an outside referee first was, as late as the 1960s, "quite rare." Then government money poured into research after the Second World War, funders convened reviewers to make sure they weren't wasting money on foolish proposals, that funding turned into a deluge of papers, and journals that had previously struggled to fill their pages began struggling to choose. Then it became universal.
Adam Mastroianni's observation is that this amounts to a sixty-year experiment humanity ran on itself, and ran badly — no randomization, no control group, nobody responsible, nobody measuring. So he went and found the report card. Scientists collectively spend about 15,000 years reviewing papers every year. In three studies where major flaws were deliberately planted in manuscripts, reviewers caught 30%, 25%, and 29% — and the planted flaws were at the level of "claims to be a randomized controlled trial but isn't," "the graphs plainly show no effect," "the conclusions are totally unsupported by the data."
The ugliest item isn't a statistic, it's a behavior. One editor began asking authors to supply raw data after submission, and half of them retracted their submissions. His conclusion, in his own words: this suggests "a possibility that the raw data did not exist from the beginning."
Meanwhile roughly 30,000 journals publish something like 4.7 million articles a year, all of them stamped as peer reviewed.
Adam Mastroianni is an experimental psychologist who finished his psychology PhD at Harvard in 2021 under Dan Gilbert. He started in 2016, which matters: that was the bottom of psychology's replication crisis. He describes finding "a bunch of sunken-eyed grad students shuffling around shellshocked, as if their parents had just called and said 'we never really loved you, it was all a big prank, goodbye.'"
He also performs and teaches improv comedy. He appeared on a British reality cooking show. He was in a film that scored 3% on Rotten Tomatoes, and wrote a post titled "This movie has a 3% on Rotten Tomatoes and I'm in it." He has done 126 escape rooms and knows perfectly well you don't care. Every post carries a photograph at the top with the same tiny credit line: photo cred: my dad. The first one is a group of escaped pigs standing in front of a McDonald's.
The blog opened on 1 January 2022 and has run to 140 posts by September 2026, roughly one every two weeks, unbroken for four years and eight months. Not dormant. His first book, The Strangest Idea in the World: A Shortcut to the Future, is due from Crown in March 2027.
One thought has hounded him for years, and he states it plainly:
There's a thought that's haunted me for years: we're doing all this research in psychology, but are we learning anything? We run these studies and publish these papers and…then what? The stack of papers just gets taller?Is psychology going to Cincinnati?, 8 October 2024
He ran into it at a specific time and place. He arrived at Harvard in 2016, while psychology was collapsing in stages. It began around 2011, when a well-known Cornell professor, Daryl Bem, published nine experiments in the most prestigious journal in social and personality psychology apparently showing extrasensory perception: participants could guess where an erotic image was about to appear on screen slightly better than chance, before the computer had randomly decided. (Why erotic? Bem didn't explain. Mastroianni's gloss: "Maybe being clairvoyant requires being a little horny.") One fluke you shrug off. Nine flukes is too many flukes. Then someone demonstrated that the statistical practices everyone was using could make it look like listening to a Beatles song made undergraduates younger. Then in 2015 came the worst of it: a large group of social scientists redid 100 psychology studies and fewer than half replicated.
So he started meeting the same person at parties, and gave him a name: Kyle — the guy in his thirties who has heard one podcast, sidles up to say "oh, but none of it replicates, right?" and smirks. One of his major 2022 essays is addressed to Kyle directly. It is called "Psychology might be a big stinkin' load of hogwash and that's just fine."
His biggest disagreement with his colleagues grows from here. The field's reflex was: then we must go back and double-check every study. He thinks that makes no sense, and not out of loyalty — he thinks everyone asked the wrong question:
So I think "Do most psychology studies replicate?" is the wrong question. The right question is "Do most psychology studies matter?" and I think the answer is probably not.Psychology might be a big stinkin' load of hogwash and that's just fine, 20 September 2022
The root problem he keeps returning to therefore has two layers. The upper layer: what shape does progress in a science actually take — does it come from blocking the worst work, or from releasing the best? The lower layer, which stings more: psychology isn't yet in a position to ask that question, because it hasn't established what things it is studying or what those things can do.
Miss both layers and you'll read this blog as a funny science writer doing popularization. His actual job is to find out precisely where a field he finds uncomfortable is uncomfortable.
"The rise and fall of peer review" reads like a bill that had been accumulating for a long time, and the smallest line item says the most about his mood: he once spent an entire day emailing a journal begging to be allowed to write "years" instead of abbreviating it to "y" for no reason. That actually happened to him.
The bigger items are stacked like this. First, the system is wildly expensive and shows nothing: 15,000 years of labor annually, against research productivity flat or falling for decades, new ideas failing to displace older ones, and a pile of findings that don't replicate. Ask scientists to rate the Nobel-winning discoveries of the 20th century and they say the ones from before peer review are as good or better — and you can't even ask them to rate the Nobel-caliber discoveries of the 1990s and 2000s, because there aren't enough of them.
Second, the system doesn't do the job it claims. Beyond those planted-error studies, he offers a harder piece of evidence: fraudulent papers get published constantly. If reviewers were doing their job we'd routinely hear "Professor von Fraud was fired today after trying to submit a fake paper." We never hear that. Every fraud story starts with the paper passing review and being published, and only later does some good Samaritan — often someone in the author's own lab — notice something weird. One reason is plain to the point of comedy: reviewers almost never look at the data behind the papers they review, which is exactly where errors and fraud live. Most journals don't require you to make data public at all; you're supposed to provide it "on request," and most people don't. Which is how we ended up with roughly 20% of genetics papers having useless data because Excel autocorrected gene names into months and years.
Third, and most cutting: scientists themselves don't believe in it. They say they take it seriously, but watch what they do. When a paper is rejected they usually don't run more experiments and rewrite — they submit the same paper to the next journal; his own undergraduate advisor explained there's a "big stochastic element" in publishing, and that the way to win is to keep stuffing the box with tickets. Once a paper is published, the reviews are shredded, and nobody cares what the reviewers said or how the authors responded — which suggests nobody thought the reviews mattered. Meanwhile they read preprints, working papers and blog posts, use unreviewed Pew and Gallup data, and attend talks on unvetted projects without ever turning to each other and saying, "So interesting! I can't wait for it to be peer reviewed so I can find out if it's true." Occasionally someone says the quiet part out loud, like the Nobel laureate Sydney Brenner:
I don't believe in peer review because I think it's very distorted and as I've said, it's simply a regression to the mean. I think peer review is hindering science. In fact, I think it has become a completely corrupt system.quoted in The rise and fall of peer review
Then he offered an alternative, and this step is the hinge of the whole thing — because he didn't theorize first and then look for a case. He did it first. In November 2022 he published a formal eight-study paper as a blog post: written in normal language, jokes included, all materials, data and code public, and one confession that would be unpublishable in a journal — he couldn't remember why he'd run one of the studies. He figured he'd look like a total dummy and be ignored. Instead, before he'd announced it, thousands of people had read it, strangers sent thoughtful reviews, tenured professors sent ideas, NPR called, and it out-read his last paper in PNAS.
That step bought him more than applause. He wrote a follow-up to deal with the echo: a tenured professor hinted she might try to get him fired; a person with a PhD accused him of "cynical metacognitive polywaffle"; he got weird, vaguely threatening emails, one containing a screenshot of his personal website with his improv experience highlighted, as proof that he is literally a clown — which, he concedes, is true. In that follow-up he also tightened his position by one notch, and the notch matters:
At its core, this is an argument against scientific monoculture. Why should everyone publish the same way?The dance of the naked emperors, 27 December 2022
Four months later he found the distinction that put everything in place. He realized the argument he kept having wasn't about a procedure but about a model of how science produces things. There are two kinds of problems: weak-link problems, where overall quality depends on how bad the worst stuff is, and strong-link problems, where it depends on how good the best stuff is.
He explains the distinction entirely in pictures. Food safety is weak-link: you don't want to eat anything that will kill you, so it makes sense for the FDA to inspect plants and set standards — the cost being that you don't get to eat casu marzu, the Sardinian cheese with live maggots in it. Music is strong-link: you listen to what you like most and never learn the rest was released. So an FDA for music would be a catastrophe — imagine having to earn a musicology degree, or memorize the sharps in A-sharp minor, or demonstrate competence with the oboe, before uploading a song. You'd wipe out most of the great stuff and get music that checks every box and stirs nothing.
His judgment: science is a strong-link problem, and everyone manages it as a weak-link problem. The history of science is littered with dead theories — phlogiston, phlegm, the luminiferous ether, geocentrism, measuring character by skull bumps, barnacles turning into geese, invisible rays shooting out of eyes, and little dudes curled up inside sperm cells. What we believe now is not a random mix of the dumbest and smartest ideas in human history, because the smarter ones stuck and the dumber ones went nowhere. He adds an important qualification: science being a strong-link problem doesn't mean science is currently strong — he thinks we're still in the Dark Ages, just less dark than before.
And weak-link gatekeeping carries a symmetrical cost that never enters the ledger, because it makes no sound. This is the sharpest sentence in his body of work:
It's even easier to never think about the strong links that were prevented from existing. The terrible study that gets published sounds like nails on a chalkboard, but the terrific study that never got funded sounds like nothing at all. Purge all the terrible at the cost of the terrific, and all you're left with is the mediocre.Science is a strong-link problem, 11 April 2023
He also supplies the best empirical support for the thesis, and the support is itself a genre. One of his favorites, he says, is "Nobel Prize winner explains how it would be impossible to do their Nobel Prize-winning work today." Peter Higgs says he wouldn't get an academic job now and wouldn't be regarded as productive enough. Brenner, on Frederick Sanger — two chemistry Nobels — notes that Sanger published little of import between insulin in 1952 and his first RNA sequencing paper in 1967, with another long gap until DNA sequencing in 1977; some committee today would flag him as unproductive and cut his modest support. Brenner's conclusion: "We no longer have a culture that allows individuals to embark on long-term—and what would be considered today extremely risky—projects." Carol Greider says she isn't sure she'd have gotten funding in the current climate to do the work that led to her Nobel, since her early work was well outside the mainstream.
This thread starts earlier than peer review. The blog's first real post, 11 January 2022, is its manifesto: "Psychology is experimental history," with a one-line subtitle — To understand humans, try bothering them.
His starting point is modest: nobody really understands what psychologists do. At parties he has to begin with what he doesn't do — I'm a psychologist but I don't treat patients, I can't figure out what's wrong with your mother, I can't prescribe you anything. Then he explains that he spent much of five years asking participants to have conversations and then asking them when they'd wanted those conversations to end. People say "So, uh, what…what do you learn from that?" and gently drift away to talk to someone else.
His answer is an analogy that functions as a hard claim. History is the attempt to tell true stories about humans; so is psychology — the difference being that historians wait for stories to happen and psychologists make them: construct a situation, put humans in it, record what happens.
The base unit of mass is the kilogram, the base unit of length is the meter, and the base unit of history is the story. […] The base unit of psychology is also the story.Psychology is experimental history, 11 January 2022
This is not decoration. He extracts a working instrument from it: delete the people from a finding, replace them with abstractions, and see what's left. His paired examples are brutal. The journal sentence reads "Self-efficacy moderates the link between performance desire and performance"; excavate the humans and it reads "The people who did well were the people who both wanted to do well and thought they could." The journal sentence reads "Ego depletion exists"; excavated, it reads "When people forced themselves to do stuff, they eventually got tired." The point isn't that the excavated version is clearer. The point is that only the excavated version lets you see how boring the finding is. Replace people with abstractions and you lose the ability to judge whether a story is any good.
Holding that instrument, he turned back in September 2022 to the replication crisis and his confusion acquired a shape. The field's panic assumes a picture: doing science is like building a majestic castle of stone, every finding a block laid on another, so a bad block threatens the whole structure. Psychology, he says, isn't like that:
There is no grand unifying theory. We have a few local theories, but mostly we have no theory at all. So we don't have a majestic castle where every stone is stacked on top of another stone; we have a few stone huts and tons of individual stones scattered everywhere.Psychology might be a big stinkin' load of hogwash and that's just fine, 20 September 2022
So replicating a psychology study is like kicking one of those stones, watching it shatter into a million pieces, and announcing, "Aha! Nothing can be built on this!" — but nothing was built on it.
He didn't stop at the metaphor; he counted. He pulled up his own recent papers and tallied how many citations were critical, meaning his paper would be in trouble if you took that cited paper away. The answer was about 15%, and half of those were the statistical software. He explains in passing why papers are stuffed with superfluous citations: mainly to please reviewers — and some of the people you cite may end up reviewing you, and they will be looking for their names.
The real turn came two years later. In the October 2024 essay he describes returning to these questions "again and again and again," and finally understanding what he'd been doing wrong: he had been judging psychology's progress by feel, which is the equivalent of sitting on that signless bus, glancing out the window and saying, "I dunno, kinda feels like we're headed toward Arkansas." The right first move isn't a verdict, it's: how could we know we're getting closer to Cincinnati?
He built five yardsticks and applied them one at a time. The first one passes: overturning folk intuitions, which psychology does extremely well — he says essentially all of psychology's progress can be summed up as "overturning intuitions," and that all of his own work fits that mold, including the illusion of moral decline, widespread misperceptions of long-term attitude change, whether conversations end when people want them to, and the liking gap.
The other four fail, and each failure comes with an uncomfortable comparison. Second: we're still losing to bullshitters. In a large competition testing ways to reduce animosity between Democrats and Republicans, one of the top performers was a 2017 Heineken advertisement — made not by psychologists to help people get along, but by marketers to sell beer. Personality psychology fares worse: someone pitted the Big Five against the Enneagram and the Myers-Briggs to see which better predicted participants' actual lives (married, own a home, convicted of a crime, meditate daily, lots of friends). The Big Five won, but part of its lead came from statistics rather than psychology — it uses continuous scores while the others collapse everything into four letters or one number, throwing away data. Use continuous scores throughout and the Big Five's lead narrows or disappears. He writes that he broke out in a sweat: after millions of dollars and thousands of studies, we are not obviously better at predicting life outcomes than people who did none of that.
Third: we have a hard time using our knowledge to do anything. Meta-analyses suggest we're no better at treating youth mental illness than fifty years ago, and no better at treating adult depression. Of the 298 disorders in the DSM, zero have been cured. Behavioral science's flagship achievement is the "nudge," and at least twelve countries have set up nudge units — but in 2022 a group of psychologists ran a "megastudy" trying 53 interventions to increase gym attendance. These are the best people in the business, well funded, trying to get people to do something they already do and want to do more of. Fewer than half the interventions worked, and when experts in behavioral science and public health tried to predict which would, they did no better than chance. His analogy: if I hired a plumber to install a toilet and he said "sure, I'll install 53 different toilets and then check which ones flush," I'd get another plumber.
What matters is that his conclusion isn't pessimism but a judgment about age:
When I look at the progress psychology has and hasn't made, I don't come to the conclusion that we're dumb; I come to the conclusion that we're young.Is psychology going to Cincinnati?, 8 October 2024
This, he says, is his fundamental disagreement with many colleagues, who seem to think the field is in middle age or beyond — which would explain their eagerness to fact-check the legacy and insist every new thing fit neatly with everything already done. If instead you think the field hasn't hit puberty, you let yourself entertain far stranger thoughts, like "How might we finally grow up?"
In May 2025 he stopped complaining and started building. His opening line: it's time to stop whining and start building, and that time is now. First he pins down "paradigm," a word used for everything: a paradigm is made out of units and rules — it says the part of the world I'm studying is made up of these entities, which can do these activities. Doing science is therefore a lot like reverse-engineering a board game: you have to work out the units in play (the tiles in Scrabble, the top hat in Monopoly) and what they can and can't do. You can spell BUDDY or TREMBLE but not GORFLBOP; the top hat can sit on Park Place or the B&O Railroad, but never inside your left nostril, or you're not playing Monopoly anymore.
With that yardstick he sorts research into three kinds, only one of which is science. Naive research has no inkling of units or rules — screw around and find out: does hair parted on the right look better, does thinking about networking make people want soap. You can do it forever without progress: if you're trying to figure out how cars work, you can ask "does the car still work if we paint it blue," then "okay, does it still work if we paint it a slightly lighter shade of blue?" Impressionistic research invents hand-wavy words and then studies them — does "mindfulness" cause "resilience" by increasing "zest for life." His diagnosis of this one is fatal:
What is "zest for life"? It is literally "how you respond to the Zest for Life Scale". And what does the Zest for Life Scale measure? It measures...zest for life. If you push hard enough on any psychological abstraction, you will eventually find a tautology like this.New paradigm for psychology just dropped, 13 May 2025
So what units is he willing to bet on? He backs a book by two pseudonymous writers called Slime Mold Time Mold, The Mind in the Wheel: the mind is made out of control systems. The classic control system is a thermostat — set a target, detect a lower temperature, turn on the heat; the gap is the "error," and the job is to minimize it. The mind probably contains many of these, because they are a very good way not to die: humans are fragile, and lots of variables have to be held at just the right level.
The framework's most provocative move is redefining emotion: an emotion is the error signal of a control system. Hunger is the error from the Nutrition Control System, pain from the Body Damage Prevention System, loneliness from the Make Sure You Spend Time With Other People System. He draws out one lovely prediction: "need to pee" will probably turn out to be an emotion, since it looks like the error signal of some Urine Control System. And "hunger" will probably split into several emotions, one per macronutrient — if one of them is specifically for sugar, that explains why people mysteriously have room for dessert after finishing everything else: the protein, carbs and fiber systems are satisfied, and the sugar system is not.
Then comes his stance toward his own proposal, which is the most portable methodology on this page:
So far, I've been talking like this cybernetics thing is mostly right. To be clear, I expect this to be mostly wrong. […] That's fine! The point of a paradigm is to be wrong in the right direction.New paradigm for psychology just dropped, 13 May 2025
From there he adds a notch to Popper. Popper said real science is falsifiable; Mastroianni says that isn't enough — real science is overturnable. Before something is worth refuting it has to be worth believing. "I have two heads" is falsifiable, but you'd be wasting your time falsifying it. He invokes Cunningham's Law — the best way to get the right answer on the internet is not to ask a question, it's to post the wrong answer — and says science works the same way: the bolder our wrong answers, the better our right answers. His evidence is his own field's history. The last time psychology leapt forward was when behaviorism went bust. Say what you like about Watson and Skinner, at least they believed in something — their ideas were so strong and specific that a whole generation launched careers by proving them wrong. That is what being wrong in the right direction looks like: when your paradigm finally falls, it sinks to the bottom of the ocean like a dead whale and an entire ecosystem grows up around the carcass. After killing behaviorism, psychology replaced it not with equally overturnable beliefs but with "anything goes" — so decades of findings each went into their own cubbyhole, and nothing was ever overturned, only forgotten.
His two best research projects share a shape: he guesses wrong first, and his own data walks him somewhere stranger.
The first one starts with omelets. Some scientists, he says, get their ideas beholding the wonders of the cosmos; some get them hacking through the Amazon with a machete; he gets his eating omelets with his friend Ethan. That day at the diner they were trying to work out why some things seem good and others bad — why do people hate Congress and love their phones? Their hypothesis was elegant: judgments are built on comparisons, and the comparison is whatever pops into your head. So Congress seems bad because it's easy to imagine it being much better (for starters, fewer villains), while phones seem great because huge improvements are hard to imagine — even a far better battery wouldn't take a phone from terrible to amazing. It would also explain why people get so angry about things they can't change but can easily picture improved: Congress, nuclear war, traffic.
Then they ran the studies. In his words: they were totally wrong. The real result was weirder — when people imagine how things could be different, they almost always imagine how things could be better.
The design is clean. First they had 91 people list things they think about or interact with regularly, kept everything mentioned by six or more, and ended with 52 items from "your phone" to "people" to "the economy." Then they asked another group how a few randomly assigned items could be different, and how much better or worse that change would be, from -3 to +3. He calls the result shockingly clear: every one of the 52 items came out above zero, with no exceptions, and not one confidence interval crossed zero. Ninety percent of participants, on average, imagined improvements — which he notes basically never happens in psychology, since even asking "would you rather get five dollars or get hit in the head with a wrench" leaves a few percent choosing the wrench.
The best data point comes from the highest-rated item. Asked how good things are right now, pets came first — rated above vacations, above friends, above "happiness" and "love." Then: how could pets be different? Answers included "Be patient when it comes to food," "Healthier/less likely to get sick," "It would be cool if they could talk." And one participant said:
"They could be immortal."Things could be better, 15 November 2022
What follows is a chain of hole-plugging studies, and the chain is the best part of the piece. Are people just complaining? No — asked how good these things are now, people happily said many were great; only news, politics and coronavirus came out negative. Is it optimism bias? Doesn't look like it — optimism is believing things not only could get better but will, and the most common probability participants assigned to their own imagined improvements was 0%. Did people hear "different" as "better"? That's the most plausible, and they checked: a slight majority did read "different" as a request for improvements. So they re-ran it asking how things could be "better or worse" and "worse or better" — no difference whatsoever; the ratings were virtually identical across all three wordings. Is it an American thing? They ran it with 95 Polish participants: same. Then they had the whole study translated into Mandarin and ran 307 Mandarin-speaking participants living in China, swapping Google for Baidu — every single item, exactly the same result.
The last study delivers the strangest wrinkle. Paying a small bonus for listing more ways than average, participants assigned to imagine "better" came up with 5 ways on average, while those assigned "worse" or "different" came up with 5.5. Which means imagining improvements is actually harder — and people do it by default anyway.
The finding hands an old puzzle a new answer. Everyone knows about the hedonic treadmill: once you're moderately happy it's hard to get happier. But nobody had really explained why. People say "you get used to good things" — which he points out is a description, not an explanation, since you still have to say why. His answer: people get used to good things because they're always imagining how things could be better. So even when things improve you may not feel better. In a cramped apartment you dream of a house; with a house you dream of a second house, or lower property taxes, or a hot tub, or two hot tubs, and so on forever.
Note that the form of this piece and its content are the same thing: it is the paper — published on a blog, with full data, materials and preregistrations, and a citation line telling you how to cite it. At the end he explains why a journal couldn't run it: in a journal you're not allowed to say "we don't know why this happens," you're not allowed to admit you forgot why you ran a study, and you are DEFINITELY not allowed to talk about Dyngus Day. You're supposed to be very serious — a reviewer once literally told him his paper was "too fun" and that he should make it more boring.
The second project's motive he states even more directly: this paper was born out of spite. His whole life he has listened to people bemoan the demise of human goodness — "used to be you could trust a man's word," "back in the day you didn't have to lock your doors," "people don't care for one another anymore." It drives him nuts because people are often wrong about how the present differs from the past; in another paper he had people estimate how public opinion had shifted over time and found they weren't just randomly wrong but biased — like everybody's darts landing six feet north of the target. He wants to grab them by the lapels and shake them: How do you know? Did you watch a season of Mad Men? Did you hear a random anecdote from your grandpa? People spend years trying to figure these things out, but you can just kinda intuit it?
He and Dan Gilbert split the question in three: do most people think this, or is it a vocal minority of curmudgeons? Could the curmudgeons be right? And if they're wrong, why do they think it?
The first part they settled by brute force: they scoured databases for every survey ever asking people about perceived moral change, excluding those about specific groups ("is the Wisconsin legislature more ethical than it used to be?") and those about issues where people reasonably disagree on what counts as bad ("are there more swear words on TV?"). That left 177 US surveys with 220,772 respondents; on 84% of them, a majority said morality had declined. Plus 58 surveys from 59 other countries, 354,120 people, with the same result: in every country Pew asked in 2002 and 2006, a majority called moral decline at least a "moderately big" problem. One incidental finding matters especially: the proportion of people perceiving decline hasn't changed across decades — as many say it today as a generation ago. Nor is it the property of the old or the conservative: older people report more total decline, but divide by age and older and younger people give the same rate; conservatives perceive more, but even the strongest liberals agree it's happening.
The second part is where the paper's weight sits. There are no moral thermometers and you can't drill ice cores for ancient levels of morality, so they used what exists: for decades survey companies have asked things like "were you treated with respect all day yesterday," "are people generally helpful, or are they looking out for themselves," "in the past month, have you helped a stranger who needed help." If morality had been falling for decades, changes should be easy to find. They found 107 surveys, 4.4 million people, 1965 to 2020, ran the tests, and found no meaningful change at all. Sometimes the indicators ticked up, sometimes down, on average nowhere. Outside the US, another 33 surveys with over 7.3 million respondents: also no change. He singles out one Gallup chart: in the same survey, every single year, about 70% of people say morality is getting worse — and every year people give the same answers.
The third part is his proposed mechanism, which he calls BEAM, assembled from two separately established phenomena: biased exposure (people pay disproportionate attention to negative information, and media companies make money supplying it) and biased memory (the negativity of negative information fades faster than the positivity of positive information — the Fading Affect Bias). The first makes today always look outrageous: murder and arson and fraud, oh my. The second makes yesterday's outrages seem less outrageous now. When things always look bad today and brighter yesterday, he says, congratulations pal, you've got yourself an illusion of moral decline.
The beautiful part is that it predicts its own exceptions. Reverse biased exposure — have people mainly hear about the good things others do — and you should get an illusion of moral improvement. They guessed this would happen in people's personal worlds, since most people probably like most of the people they deal with daily. So they asked the same participants twice, first about people in general, then about the people they interact with personally. About people in general the answers came back as before: worse overall, the same individuals worse, young people worse than the old people of fifteen years ago. But about people they knew personally, something new appeared: they said the individuals they'd known for fifteen years were more moral today. The second prediction is that switching off biased memory should kill the illusion — and you can switch it off by asking about years before someone was born, since you can't have memories from before you existed. They re-ran an earlier study asking people to rate people in general today, in the year they turned 20, in the year they were born, twenty years before that, and forty years before that. The answers amounted to saying:
People said, basically, "moral decline began when I arrived on Earth"The illusion of moral decline, 7 June 2023
How he closes the piece is more memorable than the findings. He points out that he has just shown you data from more than 500,000 people asked whether morality has declined, and virtually none of them answered "Gosh, I don't know" — even though, for them, that was the right answer. They don't know. It took him and Gilbert years and another 12 million people to arrive at a barely decent answer, which is "probably not." And yet an answer came to everyone's mind effortlessly, and they were happy to share it and to defend it when pressed. The past is a foreign country, but we all have the vivid delusion that we've lived there for a long time and know everything about it.
Then he makes the danger explicit. It's fine to have strong opinions about things you know nothing about — that's kind of what the internet is for. It stops being fine when those opinions become demands for actual changes in the world. If you think morality is declining, you must think some switch has been flipped in society causing it to produce worse humans, and you'd want to un-flip it: smash the social media companies, kill all the politicians, ban the bad books. None of it will reverse the trend, because the trend doesn't exist. It's like activating the sprinkler system in a building that's not on fire.
What's most portable from a long-running writer is usually not the conclusions but the moves. Several of his are genuinely transferable, and all of them come out of the posts above rather than from some vague claim that he's rigorous.
Ask "how would we know" before "is it true." The real value of the Cincinnati essay isn't the five yardsticks; it's that he admits he had been skipping a step for years, judging progress by feel. His self-diagnosis is that you have to first ask how you could know you're getting closer. That step almost always gets skipped, because it produces no conclusions — only criteria.
Count the thing nobody counts. His evidentiary style isn't citing an authority, it's totalling something up: 15,000 years of reviewing a year; 177 surveys and 220,772 people; 107 surveys and 4.4 million people; 52 items with zero exceptions; 15% critical citations in his own papers, half of them statistical software; 298 disorders in the DSM and zero cures. What these numbers have in common is that they were all lying in the open and nobody had bothered to add them up.
Treat abstract nouns as the prime suspect. He has two specific moves here. One is excavating the people from a sentence to see what's left ("Self-efficacy moderates the link between performance desire and performance" → "The people who did well were the people who both wanted to do well and thought they could"). The other is pushing hard on any psychological noun to see whether it collapses into a tautology (zest for life → the Zest for Life Scale → zest for life).
Hunt mysteries, not effects. The second path he proposes for his field is to really shake things up, and the way in is listing self-evident phenomena — things that definitely happen but that we cannot explain. His own list tells you a lot about his taste: the average American watches 2.7 hours of television a day, and we write it off as "leisure" as if that were an explanation — so why is it fun to watch someone make a salad on TV? Why do some people find it fun to stare at a person spinning a wheel and buying vowels while others find it fun to stare at vampires kissing? Why can an episode of Paw Patrol stop rampaging toddlers in their tracks? Making that list, he says, was hard — "kind of like trying to imagine a color you haven't seen before." What he wants is not "how do we reduce scores on the Modern Racism Scale by 10%" but "people do this weird thing…WHY."
Publish the failures and the forgetting. "I don't remember why we ran this study" appears in the body, not the cutting-room floor. "We were totally wrong" is the third paragraph of that paper. "I expect this to be mostly wrong" sits right next to the paradigm he's recommending. This isn't a pose of humility; it's his own "overturnable" standard applied to himself.
Don't write from bitterness. His essay on writing contains a rule that is the best passage in it:
All emotions are useful for writing except for bitterness. […] Other emotions—anger, fear, contentment—are deep enough to snorkel in […] Bitterness, on the other hand, is three inches of brackish water. Nothing lives in it. You can stand in it and see the bottom.28 slightly rude notes on writing, 29 April 2025
And the one that ties it together: bring your own helmet. In 2026 he wrote that everyone now says the incentives are bad, and that the diagnosis has become the universal explanation for everything from climate change to polarization to scientific malfeasance — "sorry pal, you've got a bad case of the incentives." He doesn't disagree with the analysis; he objects to what it implies, namely that incentives ought to be obeyed, that obeying them is normal or even noble, and that doing otherwise is close to impossible. His rebuttal is short: incentives are for losers. Doing something because an arbitrary reward system will give you a little treat is for pigeons, not people. What a person should do instead is acquire a purpose — refine your sense of right and wrong, then work out how you personally can increase the right and decrease the wrong. If you leave a void where your moral convictions should be, he says, that cavity fills up with tumorous desires for money, power, fame and status. And those are exactly the people most insistent that the incentives must be obeyed: like the government of a failing nation, they must swear their currency is real and lash out at anyone trying to participate in an alternative economy, lest the whole fraud come crashing down.
He has been answered seriously, by Dan Elton — a physicist by training with 42 peer-reviewed papers of his own. On 22 October 2024 Elton published "A Defense of Peer Review" in Asimov Press, prompted by Ben Recht asking on Twitter whether anyone had made a positive case for peer review; Elton looked, couldn't find a comprehensive steelman, and wrote one. He says up front that he found, and continues to find, many of Mastroianni's arguments compelling. Then he lands several blows, and the heaviest falls exactly on the soft spot of the strong-link thesis.
That blow is pathological science, Irving Langmuir's term: a bold exciting claim published with evidence that has a small effect size or sits just on the edge of significance, after which scientists spend years chasing confirmation. Elton counts the resources: 300 papers were written on N-rays, 500 on polywater, 3,200 on cold fusion. That is a direct answer to the most comfortable line in the strong-link argument — that the bad stuff barely matters. Bad ideas are not silence; they eat decades of people and money, and sometimes whole careers. Elton's conclusion is that the established experts running peer review may indeed resist paradigm-shifting work, but they also help us suss out blind alleys and steer research in more productive directions. Mastroianni does concede in the strong-link essay that worse ideas "can soak up resources and waste our time" — but he never sizes that bill. Elton sizes it.
Elton's second blow is closer to the skin: he went and counted the comments on Mastroianni's own showcase demonstration of open review.
It is also worth pointing out that only 5-10 percent of the comments on Mastroianni's paper provide criticism or potentially useful feedback from a scientific perspective. The vast majority are voicing agreement or giving praise.Dan Elton, A Defense of Peer Review, Asimov Press, 22 October 2024
This matters because the demonstration is his entire positive case: I uploaded a PDF and good things happened. If only a tenth of those good things is the thing a reviewer was supposed to supply, the demo proves his post travelled well, not that open comment can replace review. Elton adds two fair qualifications: the paper was on an accessible, mass-appeal question in human psychology, and a paper on a new immunotherapy method or a novel quantum material might struggle to incite similar engagement; and Mastroianni's audience was likely much larger at the time than that of the average new researcher. In Elton's words, it is not at all clear that papers uploaded to the internet can on their own guarantee highly-qualified readership and reach those among them willing to leave comments. Put bluntly: the sample size is one, and the sample came with an audience.
Beyond that, several problems he hasn't addressed head-on.
The strong-link frame is hard to falsify — by his own standard for science. His argument has a structure in which present mediocrity is attributed to the strong links that were prevented from existing, and those "sound like nothing at all." As rhetoric that's superb; as a claim it is very hard to argue with, because any state of affairs can be explained by what failed to appear. He says real science must be overturnable. What would overturn "science is a strong-link problem"? He doesn't say.
He demolishes better than he builds, and he knows it. He has been dissecting psychology since 2022, and by 2025 the positive program he can recommend is someone else's — a book by two pseudonymous writers — and he expects it to be "mostly wrong." "Wrong in the right direction" is defensible philosophy of science, but it is also a very convenient position: if it fails it wasn't yours, and if it works you were the earliest advocate.
He publishes inside the system too. He puts this in a footnote himself, and puts it well: the moral decline paper appeared in Nature, and the footnote says "I know it's odd for me, Mr. Rise and Fall of Peer Review, to be publishing in a peer reviewed journal" — then explains the paper was submitted in July 2022, and that his experience getting it published is part of why he wrote the post. That's the honest way to handle it, but it also shows his positive program isn't yet sufficient even for him: his dissertation entered the scientific record through the old channel.
And the harshest criticism of him was written by him. In the essay addressed to Kyle at the party, he turns the knife around, and the passage is the best evidence of how honest he is:
I'll accept this description myself: it's not clear that my own work matters. […] But if you just don't care, I don't have anything objective that will convince you.Psychology might be a big stinkin' load of hogwash and that's just fine, 20 September 2022
In the same passage he admits he believes some things are more important than others in a way that transcends human opinion, that there is no objective way to prove it, and so — in his words — "It's a religious belief, Kyle, I'll admit it." That confession is simultaneously his biggest weakness and the most trustworthy thing about him. Underneath his entire program for how science ought to be done sits an unprovable value judgment: some questions matter more than others. He doesn't pretend there's an argument there.