The number is 2.25. It's the loss aversion coefficient from cumulative prospect theory, the figure behind the claim that a loss hurts roughly twice as much as an equal gain pleases. It gets quoted like a physical constant.
It came from 25 graduate students answering hypothetical questions in 1992.
Thirty years of work has since tried to pin the number down properly. The best-known effort pools 607 estimates and lands near 1.96. A re-analysis of that same dataset, splitting it by how the questions were designed, gets 1.07 in the cleanest subset. A separate meta-analysis that refits the model to raw individual choices gets 1.31. And a representative survey of 3,000 Americans finds about half of them aren't loss averse at all.
So the coefficient isn't a constant. It's a contested parameter, and the size of the dispute is bigger than most people who cite 2.25 realise.
Where 2.25 came from
Kahneman and Tversky's 1979 prospect theory paper didn't give a number. It gave a shape. Value is defined over gains and losses from a reference point, not over final wealth, and the curve is steeper below the reference point than above it. Their words were that losses loom larger than gains.
They also made a claim that matters for everything that followed. Symmetric fair bets get less attractive as the stake grows, they wrote, so someone who'd shrug at a coin flip for a pound might refuse the same flip for a hundred. Loss aversion was never presented as a fixed multiplier that applies identically at every size.
The 2.25 arrived with the 1992 follow-up that formalised cumulative prospect theory. The loss aversion meta-analysis by Brown, Imai, Vieider and Camerer documents how that estimate was produced: preferences elicited from 25 graduate students at elite west-coast American universities, across three sessions of unincentivised lottery choices. The reported figure was a median. No mean and no measure of dispersion were published alongside it.
That's a thin foundation for a parameter that now appears in behavioural finance simulations of the equity premium, the disposition effect and asset pricing. The meta-analysts quote Barberis and co-authors making exactly this complaint about their own practice: the estimates are almost 30 years old, rest on a small number of participants, and it seems prudent to base the values on a wide range of studies rather than one.
What 607 estimates say
Brown and colleagues assembled every empirical estimate of the coefficient they could find in economics, psychology, neuroscience and several other fields, reported between 1992 and 2017. That gave 607 estimates from 150 articles, published as a Journal of Economic Literature meta-analysis in 2024.
The raw distribution is right-skewed. The median reported estimate is 1.69, the mean 1.97, and 93.9% of estimates sit above 1. The full range runs from 0.04 to 23.46, which is itself a warning about how much the measurement method drives the answer.
Their preferred hierarchical model puts the mean coefficient at 1.955, with a 95% credible interval of 1.824 to 2.104. A simpler specification gives 1.810. Their own reading is that 2.25 seems a bit too high, and that the credible intervals exclude both 1 and 2.25.
Two caveats travel with that headline. First, the dataset is dominated by published work, and their meta-regression predicts coefficients about 0.27 points lower in working papers, roughly 1.7, though the difference isn't statistically significant at 5%. Second, the heterogeneity is enormous and no single design feature explains it. Estimates from non-university populations and field experiments run modestly higher, and that's about the strongest pattern in the data.
How the number gets measured
Almost every estimate comes from asking people to accept or reject a list of 50:50 gambles with one gain and one loss, then finding the loss size at which they flip. The design of that list turns out to matter enormously.
Take a real example. Mrkva and colleagues asked participants about investments offering a 50% chance of winning $100 against losses of $10, $25, $50 or $100. The gains and losses aren't symmetric, and the losses climb in order. Zeif and Yechiam worked out what that does to the arithmetic: someone answering completely at random on that list produces a mean coefficient of 3.47. Noise alone looks like strong loss aversion.
That's not a small technical quibble. It's the difference between measuring a preference and measuring a questionnaire. The same critique covers ordered presentation, which invites people to pick a cut-off in the middle of the list, and accept-or-reject framing, which tangles loss aversion with a preference for doing nothing.
The problem also runs the other way. Walasek, Mullett and Stewart tried to refit cumulative prospect theory to raw individual choices rather than pooling published headline numbers. They found only 29 papers with suitable data and, after chasing authors for files that had been lost or couldn't be shared, ended up with 19 datasets from 17 published articles. Their weighted median coefficient is 1.31, with a confidence interval of 1.10 to 1.53 that excludes 2.25.
The more revealing detail is in the individual studies. Their per-study estimates ran from 0.65 to 3.45. The confidence intervals included loss neutrality in 12 of the 19 datasets, and included 2.25 in only six. Their own conclusion is blunt: much of the available data is too imprecise to estimate the parameter at all. That's a limitation of their evidence as much as a finding about people, and they say so.
The case against loss aversion as a general phenomenon
The strongest version of the objection isn't that the coefficient is smaller than advertised. It's that there's no general phenomenon to put a coefficient on.
Gal and Rucker made that argument in a 2018 review. They open with a poll of about 80 researchers at a decision-making conference: all but three said losses loom larger, and not one said gains do. Their review then works through the standard evidence and argues that each pillar confounds losses with something else, usually action versus inaction.
Some of their examples are hard to wave away. In one experiment they cite, participants choosing between a sure zero and a 50:50 bet on winning or losing 1,000 points split 48% safe against 52% risky. A 1964 study offered a choice between a coin flip for one point and a coin flip for four points; 49% picked the smaller bet, when loss aversion predicts a clear preference for the smaller potential loss. In their own work on everyday objects, people rated gaining a mug as more affecting than losing one, 2.71 against 1.38 on a five-point scale in each direction.
The most direct evidence arrived from a representative sample. Chapman, Snowberg, Wang and Camerer ran incentivised surveys covering 3,000 US adults and found that around half were loss tolerant. The clean test is a single choice: a sure $0, or a 50:50 gamble paying $10 or costing $12. Sixty per cent of the general-population sample took the gamble, which has negative expected value. Among University of Pittsburgh undergraduates, 28% took it.
Eighty-seven expert economists asked to predict the result guessed 30% for the general population. They were right about the students and badly wrong about everyone else. Only 10% of the experts said they'd take the bet themselves. Loss aversion was more common among people with high cognitive ability, which is one reason student labs kept finding it.
Two caveats belong next to that finding. The paper circulated as an NBER working paper that hadn't been peer reviewed at that stage, and the stakes are small: $10 and $12. Whether the same people would shrug at a 50:50 bet on $10,000 is untested here, and the 1979 paper predicted they wouldn't.
Small stakes, small coefficient
Zeif and Yechiam went after the stake question directly. They re-ran the standard tasks after removing the design features that bias towards loss aversion, making gains and losses symmetric and randomising the order, across five studies with 2,001 participants.
At small amounts, nothing. For average losses up to $20 there was no loss aversion, including in a version where the money was real. At an average loss of $40 the coefficient came in at 1.16, with only 51% of participants above 1. At $100 it reached 1.54, which is loss aversion, but well short of 2.25.
Their conclusion is that the coefficient isn't constant across amounts at all. It rises with the size of the loss and falls to 1 or below when the amounts are small. Notably, they did replicate the original results when they used the original asymmetric, ordered task design, which is what makes the finding a methodological one rather than a failure to reproduce.
This is the point at which the parameter stops being a personality trait. If the number depends on the size of the loss, then anyone applying a single coefficient to a portfolio is applying a number calibrated at a scale that has nothing to do with the sums involved. The gap between a measured preference and a lived drawdown is the same gap that shows up when questionnaire risk scores are compared with actual drawdown capacity.
The re-analysis that split the evidence in two
In 2025 Yechiam and Zeif took the Brown meta-analysis dataset and re-cut it. They could classify 84 papers, 163 estimates and 149,218 participants by two design features: whether average gains and losses were the same size, and whether the items were presented in order of size.
Run across everything, they reproduce the original result, with an overall coefficient of 1.82. Split it, and it comes apart. Where losses were smaller than gains and items were ordered, the median is 2.295 across 62 estimates. Where gains and losses were symmetric and the order was random, the median is 1.125 across 22 estimates, and the modelled estimate is 1.07 with a confidence interval of 0.97 to 1.18. That isn't significantly different from loss neutrality.
They also ran a funnel-plot correction on that subset, which suggests the residual sliver of loss aversion could be publication bias, with a corrected estimate slightly below 1. Their headline is that reports of strong loss aversion are largely an artefact of how the questions were asked.
Three things should temper that. The clean cell rests on about 2,000 participants, not 149,000. One surprising result cuts against their own story: stake size wasn't significantly related to the coefficient in this dataset, which sits awkwardly beside their experimental finding that it is. And the version examined here is the authors' preprint of the Journal of Economic Psychology article, not the typeset paper.
What the defenders still have
The case for loss aversion isn't dead, and treating the critics as having won would be its own error.
Gächter, Johnson and Herrmann measured it two ways in 360 randomly selected customers of a German car manufacturer, a non-student sample. In the endowment task, the median ratio of selling price to buying price was exactly 2.0, the mean 2.62, and 88% of individuals were above 1. In the lottery task the same people gave a median of 1.5. Crucially, the two measures correlated at 0.635, which is hard to explain if the endowment gap is just people misunderstanding an unfamiliar task.
They report large variation, though. The standard deviation of the riskless measure was 2.28, the interquartile range 1.33 to 3, and they note that car customers may not be representative of the population at large. Loss aversion rose with age, income and wealth, and fell with education.
Mrkva, Johnson, Gächter and Herrmann published a reply to Gal and Rucker under the title "Moderating Loss Aversion: Loss Aversion Has Moderators, But Reports of its Death are Greatly Exaggerated". That paper sits behind a paywall and wasn't read for this piece, so nothing here characterises its evidence beyond the fact that Zeif and Yechiam replicated its results using its original task design.
And Brown and colleagues examined publication bias carefully rather than assuming it away. The funnel asymmetry they see is concentrated in studies that report their own standard errors, which is not a pattern any editorial-bias story predicts. Their reading is that it's a statistical artefact of a parameter truncated at zero.
What this means for a portfolio
Almost nothing follows mechanically, and that's the useful part.
If you want a single number for how much a loss stings, the honest range is somewhere between 1 and 2, with the wide end reserved for large sums and the narrow end for anything trivial. That range is too wide to calibrate anything. It certainly can't support the common move of assuming a client's loss aversion coefficient and deriving an equity weight from it.
The Chapman results add a second wrinkle. Loss-tolerant individuals in their sample held more of their assets in stocks, were more likely to have gambled recently, more likely to have had a recent financial shock, and had lower overall assets. Their elicitations of ordinary risk aversion showed no such correlations. Whatever gain-loss attitude is measuring, it tracks real behaviour better than a risk questionnaire does, but it tracks it in directions that cut both ways.
What survives is the qualitative point, and it's the one that shows up in behaviour rather than in a parameter. People do treat gains and losses asymmetrically, sometimes strongly, sometimes not at all, and the asymmetry is why the gap between fund returns and investor returns keeps reappearing. It's also why peak-to-trough drawdown feels like a different risk measure from standard deviation even when both describe the same series.
What would change the conclusion
Three findings would move this materially.
A large incentivised study at meaningful stakes, using symmetric and randomised items, would settle the stake-dependence question. Nothing in the current evidence tests whether the coefficient climbs past 2 when the sums are a month's salary. Both camps have been arguing over $6 lotteries.
A replication of the Chapman result in another country would tell you whether roughly half the population being loss tolerant is a fact about people or a fact about American survey panels. Their paper notes UK estimates near 1 in one study and a median of 1.26 in another, though both used different methods.
And a re-analysis that reconciles the two meta-analytic camps would help most of all. Brown and colleagues have 607 estimates and get 1.96. Yechiam and Zeif use the same dataset and get 1.07 in the subset they consider clean. Walasek and colleagues refit the model from scratch and get 1.31. Those aren't three measurements of one quantity. They're three different questions, and whoever states clearly which question a coefficient answers will have done more than another decimal place ever could.
Until then, treating 2.25 as a settled parameter isn't a simplification. It's a claim the evidence stopped supporting some time ago.