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Under review as a conference paper at ICLR 2027

LLMs as Research Participants: Households Built from Survey Records for Empirical Economics

Abstract

Using large language models (LLMs) as research participants in economics requires each simulated person to decide as a real person with the same background would, but their answers have been shown to be biased relative to real people's, and neither the source of this bias nor a reliable correction is known. We propose type sampling, which does not correct the bias but instead unfolds the one answer that has to serve many people sharing the same characteristics into the answers of the people those characteristics could describe. For 500 households from the Panel Study of Income Dynamics and seven LLM families, mean AUC on ten asset-holding questions rises from 0.66 to 0.80, and for average amounts held by groups of similar households, mean log R-squared rises from −0.08 to 0.49 across the three LLMs tested. We then set out a procedure for experiments on simulated households, with a design that keeps the two conditions the same household and criteria that their responses must meet, and apply it to Imbens, Rubin, and Sacerdote's lottery study, which the simulation also extends to prizes of other sizes and payment timings that observed data cannot provide. In the families whose responses meet our three criteria most fully, working hours fall by less than in the original study, and the division of the prize among financial assets and housing is close to the original estimates.

Primary area:
foundation or frontier models, including LLMs
Keywords:
large language models, economics, computational social science, simulated participants, household finance, silicon sampling

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_pnBuOpenReview ↗
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Paper summary

The paper deals with the problem of using llm simulated participants for economic study. Traditionally directing asking results in bias. The paper mitigate the bias by sampling multiple simulated people with plausible relevant background and average, which improves prediction.

Critical strengths
  • The bias in LLM's simulation is a important issue in applying it
  • The predictions are checked with real-world datasets
  • Plentiful ablations
Critical weaknesses
  • Lack of diagrams in paper make reading harder
  • The paper doesn't deal with simulation asking questions that don't have ground-truth answer, which are where in real life this method could be useful, and because non-existing in training data of LLM can lead to different behaviors.
  • The scope of simulation is rather narrow
Questions for authors
  • Previous works (such as https://arxiv.org/abs/2503.16527) say expanding demographcis to qualitative details like lifestyle introduce bias, which is opposite to this paper's conclusion. How would authors reconcile this.
3 comments
AuthorsOpenReview ↗

Response to Reviewer pnBu (1/2): summary, W2

Thank you for reading the paper and for the review. We first summarize each answer.

W1. We agree that a diagram makes the method much clearer, and the revision adds one (Figure 1, on the second page).

W2. The method is meant for running experiments on simulated households and estimating effects from them, and the lottery experiment (Section 4) is one on a question without a ground-truth answer. Below we separate two kinds of such questions and say where the paper makes no claim.

W3. Beyond the PSID and the lottery experiment, the paper applies the method to household-finance surveys from China and Japan, to political and social attitudes in the General Social Survey, and to two published survey experiments (Section 5 and Appendix D).

Q1. Li et al. give each simulated person one generated persona, while we average over fifty for each survey record. Part of their warning applies to our results too.

W2 (questions without a ground-truth answer). We take this point to have three parts, whether the paper contains such simulations, whether an LLM can answer questions that are absent from its training data, and where the method is useful.

On the first, the paper does contain such an experiment, the lottery experiment of Section 4. No PSID household has a correct answer to it, because no survey records what these households would have done had they won a lottery. We describe each of 200 households in 2019 twice, once as it stands and once as having won, in 2009, a prize paying 150,000 dollars a year for twenty years, and the difference between its answers under the two descriptions is the simulated effect of the prize. Since there is no answer to check each household against, we compare the estimated effect with what the literature has estimated from real lottery winners (Imbens, Rubin and Sacerdote, 2001). In the LLM families that meet our three criteria most fully, the division of the prize among financial assets and housing is close to their estimates.

On the second, we think your concern is right, and it helped us state the boundary of what the paper claims. A question can lack a ground-truth answer in two ways. In the first, no data records the answer, but the behaviour behind it is contained in what the LLM has read. In the second, the situation itself is absent from anything the LLM has read, and there we agree with you that nothing guarantees the answers. The paper makes no claim about the second kind. The lottery experiment is of the first kind, since how households work and save after receiving money is something people have written about at length.

On the third, questions of the first kind are where we think the method is useful. Such a question is still not one the LLM can simply be asked. Type sampling is not meant as a prediction model that returns an answer. As in empirical economics, a quantity such as the effect of a prize on working hours has to be estimated from a treated and an untreated group, and with real households a clean experiment of this kind is rarely available. Running such experiments on simulated households is what the method is for.

Our approach is to start where the answer is known and move outward, because if simulated people cannot be shown to answer correctly where we can verify it, there is no reason to trust them where we cannot. Aher et al. (2023) and Ashokkumar et al. (2026) take another route. They simulate experiments directly and compare the simulated results with those of the human experiments, without first comparing answers respondent by respondent. We see building outward from a validated base as part of what the paper contributes.

For the lottery experiment, Section 4 sets criteria that can be tested without knowing the answer. The simulated winners must state that they won and how much they have received, their reported wealth must reflect the prize, and their other answers must agree with that wealth and with one another.

The shared note above also reports two new experiments, which test whether the households we describe as winners behave as a treated group.

AuthorsOpenReview ↗

Response to Reviewer pnBu (2/2): W3, Q1

W3 (scope). The paper may seem to focus on the PSID and the lottery experiment, but it covers more than these two. What it covers falls into two areas, household decisions and attitudes. For household decisions, besides the PSID (United States, 2019 and 2023), we use the CHFS (China, 2011) and the Public Opinion Survey on Household Financial Behavior (Japan, 2019). For attitudes we use the GSS (United States, 2022), with 18 questions that include the 2020 presidential vote, abortion and the death penalty. We also run two experiments on human behaviour from the archive of Ashokkumar et al. (2026), and the simulated panel reproduces the direction of 32 of 36 contrasts in one of them. These results are in Section 5 and Appendix D, and the revised introduction now lists them.

Q1 (Li et al., 2025). You ask how our result can be reconciled with Li et al. (2025), who find that the more of a persona the LLM generates, the further the simulated results move from the real outcomes. The two studies use generated detail for different purposes.

In their study each simulated person receives one generated persona, and that persona then stands for the person. If the LLM writes it with a slant, the person carries the slant. In type sampling no single generated description stands for a household. For each survey record we write fifty types, which are different people that the same record could describe, take one answer from each, and combine the answers. Put another way, they condition on one generated description and we average over many. Their personas also start from age, sex, race and state, with the rest generated, while ours start from values the survey recorded, including income and net worth.

Their warning still applies to us in part. Averaging over fifty types limits the influence of any one description, but if the types as a whole lean one way, the average leans too. Type sampling reduces the holding-rate error on nine of ten questions, but the error for home ownership rises, and the error is larger for wealthy households. We have not run an experiment that separates these differences, so we cannot say which of them accounts for the contrast in results. The revised introduction adds this comparison.

Thank you for your response! I have decided to maintain my existing score.

Reviewer_4xRfOpenReview ↗
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2
Confidence
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Paper summary

This paper proposes a method for using LLMs as research participants in economics called type sampling. It aims to supplement for the limitations of survey data, which record part of the household characteristics and may omit experiences and preferences that affect people's decisions. The method prompts an LLM to generate multiple potential persona descriptions based on household characteristics and asks the simulated individuals to answer survey questions. The authors evaluate this approach through multiple tasks including household asset holdings, the prediction of asset values, an experiment concerning lottery winnings and many others listed in appendices.

Critical strengths
  1. This paper focuses on the challenges faced by LLM as a participant in simulation research. Improving the consistency between simulated respondents and real human behavior has potential value for computational social sciences and empirical economics.
  2. This type sampling methods help improve LLMs ability serving as research participants. As is shown in Table 1, compared to simulating with a comprehensive profile directly using prompts, the simulated households generated via type sampling exhibit a smaller discrepancy from the true distribution across most dimensions.
  3. This paper features extensive experiments, ranging from the proposal of the method to the validation of its effectiveness through case studies of lottery winnings, which demonstrates relatively broad applicability in different countries and beyond economics.
Critical weaknesses
  1. The difference in method contribution from existing methods is not clearly stated. Although the paper compared with single and repeated inquiries, there is still a lack of a comprehensive comparison with the existing methods and related works to demonstrate the superiority of this method.
  2. The validation of the core claim of simulating research participants is still limited. The Lottery experiment examines the internal consistency of simulated responses. But the consistency cannot prove that the estimated intervention effects truly reflect human behavior. It is not sufficiently enough to support the broader application claim of LLM as a reliable participant in economic experiments.
  3. The organization of the paper and the presentation of the results have affected the interpretability of some experimental conclusions. The paper lacks an overview of methods, and the organization of experimental chapters can be further divided and improved. Some important experiment results are mainly presented in the appendix. In addition, Table 1 reports the observed holding rates and the holding rate error, but does not provide the predicted holding rates for the main seven model comparisons. It is difficult for readers to judge the systematic overestimation and underestimation. It is strongly recommended to present the main results, limitations, and conclusions supported by different experiments in a clearer and more focused manner.
Questions for authors
  1. How does Type Sampling perform in household financial decisions experiments compared to directly requiring LLM to output probabilities and other methods of constructing household personas?
  2. Can you provide the predicted holding rates for the main seven model comparisons and analyze whether the predicted holding rates in different demographic or wealth groups match the true holding frequency?
  3. To what extent can the three consistency criteria in the Lottery experiment evaluate the reliability of simulated intervention effects? What further evidence supports the claim that these simulated responses reflect real human behavioral changes?
  4. What is the possible solutions for the two limitations mentioned in Discussion section?
  5. Could the authors improve the clarity and readability of this paper and explain why there lacks an overview figure illustrating the overall workflow?
3 comments
AuthorsOpenReview ↗

Response to Reviewer 4xRf (1/3): summary, W1

Thank you for the careful reading and for the concrete questions. We first summarize each answer, and the details follow in three comments.

W1. The submitted paper's comparisons cover three kinds of existing method: asking once, asking many times and averaging, and training on human answers. To our knowledge, none generates several different descriptions of people for one survey record and combines their answers.

Q1. Asking for a probability does not directly give amounts, which experiments need. On yes-or-no questions it ranks households about as well as type sampling, and on amounts, in a test we have now run, it does much less well.

W2, Q3. Meeting the criteria does not show that simulated effects equal human effects, and we do not claim it. The evidence we have is the comparison with real lottery winners and two new experiments, which we report.

W3, Q2, Q5. We agree. The revision adds an overview figure, and Table 1 now reports the predicted holding rates.

Q4. The first limitation was our mistake, and the revision corrects it. The second stands, and we give the explanation we have.

W1 (difference from existing methods). The comparisons in the submitted paper cover three kinds of existing method. The first gives the LLM one description of the person and takes one answer (Argyle et al., 2023; Moon et al., 2024). Asking once is the comparison throughout the paper (Tables 1 and 2), with a mean AUC of 0.66 against 0.80 for type sampling (seven LLM families, ten holding questions). The second repeats the question with the same description and averages the answers (Bisbee et al., 2024; Brand et al., 2024). Asking fifty times gives 0.71 (three LLM families, Section 3 and Appendix B.17). The third trains on human answers (Binz et al., 2025; Kolluri et al., 2025). The paper's benchmark of this kind is supervised, LightGBM trained on other households' answers, and gives 0.81 (Table 1). A fourth method, asking the LLM for a probability over the answers (Ahnert et al., 2026), is the subject of your Q1, and we compare with it there.

Most of the studies we found that compare LLM answers with individual people go in one direction. They show, each in its own setting, that the match remains limited, and several examine why (Bisbee et al., 2024; Peng et al., 2026; Ahn et al., 2026, arXiv:2608.29455; Chen et al., 2026, arXiv:2607.26348; Jia et al., 2026, arXiv:2605.10659; Pourtaheri and Zareei, 2026, arXiv:2610.03998; Wang, 2026, arXiv:2609.16395; and, for the ranking of respondents, Cummins, 2025). This paper goes the other way and offers a method that improves the match. We do not have a full account of why it works, but the comparisons above show that it does. It differs from asking once or many times in one step, which is to write several different descriptions of people for the same survey record and combine their answers.

AuthorsOpenReview ↗

Response to Reviewer 4xRf (2/3): Q1

Q1 (asking the LLM for probabilities). Asking the LLM directly for a probability is an appealing method, and it was our own first idea when we began this work. Recent work proposes it as well (Ahnert et al., 2026). It has one serious problem. It does not directly give amounts, and a method for social and economic experiments has to answer numerical questions, such as hours worked or the balance of an account, as well as yes-or-no questions. The new Appendix B.19 has results for both kinds. On the yes-or-no questions it ranks households about as well as type sampling, with a mean AUC of 0.784 against 0.800, although its holding rates are further from the survey on six of the ten questions. On amounts, which it reaches only through an indirect procedure that we designed for this response, type sampling is closer to the survey for all four assets, in both LLMs and under both conversions.

Yes-or-no questions (tested earlier, now Tables B19a and B19b). Each of the seven LLM families was asked once per household for the probability of holding each asset (two families are earlier versions in these runs). The table gives the AUC and the error in the holding rate, in percentage points, both averaged over the seven families.

QuestionAUC: probabilityAUC: type samplingError: probabilityError: type sampling
Stocks0.8560.86121.62.4
Savings0.7760.8043.93.5
Employer plan0.8640.8583.79.1
IRA0.7980.80612.54.1
Business0.7380.7482.81.5
Home0.8650.8818.712.1
Vehicle0.7770.7975.15.7
Other real estate0.7990.8003.84.1
Other financial assets0.7280.74124.216.1
Other debt0.6370.7016.25.3
Mean0.7840.8009.36.4

Amounts (run for this response, now Table B19c). A probability question cannot return a dollar figure directly. We ask instead for the probability that a balance exceeds each of ten thresholds, from 100 to 3,000,000 dollars, so that the ten answers trace the distribution of the balance and an expected amount can be computed from it. Two LLMs (DeepSeek V4.1 Flash and Claude Haiku 5.5) answered these questions once per household, without types, and type sampling for amounts was run with the same two LLMs. The table gives the log R-squared of cell-mean balances. Each probability entry has two numbers, one for each of two conversions into expected amounts that we fixed beforehand. These are single runs, scored on a held-out half of the households.

AssetType sampling: DeepSeekType sampling: HaikuProbabilities: DeepSeekProbabilities: Haiku
Stocks0.560.58−0.32, −0.07−0.97, −0.58
Savings0.900.850.12, 0.34−0.23, −0.25
Employer plan0.040.20−0.65, −0.13−0.40, −0.10
IRA0.720.63−0.12, 0.190.04, 0.13
AuthorsOpenReview ↗

Response to Reviewer 4xRf (3/3): W2, Q3, W3, Q2, Q5, Q4

W2, Q3 (whether the simulated effects reflect human behaviour). We agree with the point. Meeting the three criteria does not show that a simulated effect equals the effect on real households, and the revision states this explicitly. Our strongest claim is the first step, that simulated households answer close to real ones where the answer is known, and it is the ground for experiments on them. The criteria are conditions that must hold before a difference is read as an effect. They show, from the answers themselves, that the simulated winners registered the treatment, and that their answers agree with one another and, without the prize, with what comparable real households report. Of five LLM families, two meet all three most fully, and we interpret magnitudes for these two only.

You also ask what further evidence there is. One piece is the comparison with real lottery winners. The LLM is never asked for an effect, and no parameter is fitted to the published estimates. In Table 3 the responses of financial assets, of financial assets outside retirement accounts and of house value lie within one standard error of the estimates of Imbens, Rubin and Sacerdote, with one exception, Kimi's financial assets outside retirement accounts.

In response to this concern, we also designed two further experiments after the submission (Section 4 and Appendix E.12 of the revision), on the same 200 households and with two later LLMs. The idea is to name specific ways in which the simulated winners could fail to be a treated group, and to test each.

The first way is that a household described as a winner only gives the LLM's idea of what a lottery winner is like. The criteria cannot settle this alone, because an LLM could meet them while only repeating that idea. The most direct way to obtain that idea is to ask a household that did not win to imagine winning, so we compare the two. They differ. Whether asked before or after giving their own answers, households imagining the win report an increase in financial assets 2.0 to 3.9 times that of the households described as winners, and a fall in working hours 1.9 to 3.4 times as large. Describing a household as a winner therefore gives different answers from asking it to imagine winning.

The second way is that the treated and control groups differ in something other than the prize. If the simulation keeps the same households when the prize is set aside, winners asked to answer again as if they had not won should return, on average, close to the control group. For financial assets they do, with a gap of 1.6% and 2.9% of the effect. For working hours the gap is larger, 16% and 34% of the effect. Table E14 scores these answers against the PSID benchmark of the first criterion.

Even so, we cannot show that a simulated treated group is the same as a treated group of real people, short of giving the same intervention to both, and we do not claim it. The two experiments test two of the ways in which the simulation could be wrong, and not all of them.

W3, Q2, Q5 (organization, predicted holding rates, overview figure). We agree. Coming from a different field, we did not know how much readers here rely on an overview figure, and that was our oversight. The revision has one on the second page (Figure 1), and the abstract and the introduction are rewritten to state the steps in order. On the results placed in the appendix, the page limit forced choices, and the revision moves the predicted holding rates into Table 1.

Appendix B.18 gives the predicted rates for each of the seven LLM families. In every family, type sampling under-predicts home ownership, employer retirement plans and other real estate, and over-predicts other financial assets. The error is largest for the wealthiest households (Appendix D.1).

Q4 (possible solutions for the two limitations in the Discussion). The first limitation was our mistake. The paper says that the simulated households are less dispersed than real ones, with a variance a third to a half of the real one. That figure compared the average of each household's fifty answers with individual real households, and an average always varies less than the answers it is taken from. Counting the variation among the fifty answers as well, the total variance ratio averages 1.02 across the ten holding questions and seven LLM families (Appendix B.15), and the revision corrects Section 5.

The second limitation stands. Holding rates are off for some groups, above all the wealthiest fifth. Part of this comes from our question wording, which does not follow the survey's definitions exactly. When the same types answer questions adapted to the survey's wording, the mean absolute bias of the wealthiest fifth falls from 12.1 to 7.7 percentage points (Appendix B.9, one LLM). For the rest, one possible explanation is that wealthy households are few, and the text an LLM has read probably says less about how they hold their assets.

Reviewer_BnM1OpenReview ↗
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2
Confidence
2
Informativeness
1
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Paper summary

The authors propose and validate a method called type sampling, which involves first constructing different types, sampling from them, and then generating responses. Their experiments demonstrate that this method enables LLMs to better simulate the economic behavior of real households, outperforming LightGBM as a baseline. Building on this approach, the authors construct a panel of "simulated households" that can be used for social science experiments.

Critical strengths

None

Critical weaknesses

Previous studies have documented various issues, including bias, in the process of using LLMs to generate and sample from different types. This raises questions about the soundness of the theoretical framework.

Questions for authors

Is it possible that LLMs have learned the findings of Imbens, Rubin, and Sacerdote (2001)?

1 comment
AuthorsOpenReview ↗

Response to Reviewer BnM1

Thank you for the review. We answer your weakness (W1) and your question (Q1) below.

W1 (bias when LLMs generate and sample types, and the soundness of the theoretical framework). The paper's contribution is a method, and one the literature needs. Whether LLMs can take the place of people in social science and psychology experiments has been taken up in recent years in Political Analysis, PNAS and Nature (Argyle et al., 2023; Mei et al., 2024; Binz et al., 2025; Ashokkumar et al., 2026) and at ICML, NeurIPS and ACL (Aher et al., 2023; Xie et al., 2024; Ahnert et al., 2026). That work depends on simulated respondents who answer like the real people who share their background, and most of the studies we found that compare LLM answers with individual people report, each in its own setting, that the match remains limited (for example Bisbee et al., 2024; Peng et al., 2026). On household survey questions the paper improves this match substantially over asking once, and it does so with a simple method. It writes several different descriptions of people for each survey record, takes one answer under each, and combines the answers, which to our knowledge no earlier study does. Section 4 then shows how households built in this way can be used in a simulated experiment.

We judge the method by its results against what real households answered. On the ten holding questions it raises the mean AUC from 0.66, when the LLM is asked once, to 0.80 in seven LLM families, without being given the households' answers to those questions. A supervised model trained on the answers of the survey's other households reaches 0.81. Type sampling lowers the mean holding-rate error from 11.8 percentage points to 6.4, and on dollar amounts it raises the log R-squared of group-mean balances from −0.08 to 0.49, averaged over four assets and three answering LLMs (Tables 1 and 2). Section 5 and Appendix D report tests on other surveys.

On the bias you raise, the paper measures it against the survey. The holding-rate error above is that measure, and Section 5 and Appendix D.1 show where it remains, by wealth group.

On the theoretical framework, the paper does not offer a theory of how LLMs generate types, and we cannot say how the fifty types written for a household correspond to groups in the real population. The paper does not claim that they do (Section 3). What we did is test the design choices, each in one LLM family (Appendices B.10 and B.11). The ranking largely stabilizes from fifty types onward, and none of the weightings we tested improves both the holding rates and the ranking out of sample. None of these tests identifies the distribution of types in the population, which the survey does not observe.

Q1 (whether LLMs have learned the findings of Imbens, Rubin and Sacerdote, 2001). The question can mean two things. The first is that the LLM reproduces the published estimates from memory. The design and the results argue against recall as the sole explanation. The original study surveyed people who won the Massachusetts lottery between 1984 and 1988, and ours takes 200 PSID households in 2019 and gives them a different prize. No request asks the LLM for an effect. Each request asks for one household's answers under one condition, and the effect is computed afterwards from thousands of separate answers. The results are also not a copy. Working hours fall by less per dollar than in the original study, and the same households respond to prizes of other sizes and to a lump sum, which the original study does not report (Figure 2). The second is that the LLM knows in general how people respond to money, that they work less and hold more assets. We cannot exclude this. Such knowledge is what a simulation of people relies on, and where an LLM acquired it is a question this paper does not answer.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of the revision, and two additional experiments on the lottery households

We thank the three reviewers for their comments. In response we have revised the paper substantially, and two changes matter most.

1. An overview diagram and a rewritten introduction. The paper now has a diagram of the whole procedure (Figure 1, page 2), and the abstract and the introduction are rewritten so that the contribution and the aim of the paper are clear from the start. Type sampling is the contribution, and the lottery experiment is a demonstration of what it makes possible.

Figure 1 shows the method in three steps. First, for each household's survey record an LLM writes fifty descriptions of different people who fit the record, without being told the question, and each description answers once. The household's answer is the share saying yes, or the average amount. Second, these answers are compared with what the real households reported, on ranking, on holding rates, and on the average amounts of groups of similar households. Third, the same households are described under a control and a treated condition, and the two sets of answers are compared once three criteria are met.

2. Two additional experiments. Two reviews raise a basic question about the simulated lottery experiment, which is whether the households we describe as winners can be trusted as a treated group when no ground truth exists for their answers. We ran two experiments on this question, on the same 200 households and with two later LLMs (DeepSeek V4.1 Flash and Claude Haiku 5.5). A new paragraph of Section 4 summarizes them, and Appendix E.12 gives the design and every outcome, including those where the result is weaker.

The first experiment asks non-winners to imagine winning. The worry is that a household described as a winner only gives the LLM's idea of what a lottery winner is like. So we ask control households to imagine that they had won the same prize. Whether they are asked before or after giving their own answers, and in both LLMs, the imagined answers differ from those of the households described as winners. The increase in financial assets is 2.0 to 3.9 times as large and the fall in weekly hours 1.9 to 3.4 times as large.

The second experiment asks winners about not winning. Here the worry is the opposite one, that the households described as winners differ from the control households in something other than the prize. So after a winning household answers the questionnaire, we ask it to answer again as if it had not won. If the simulation keeps the same households when the prize is set aside, these answers should return, on average, close to the control group's. Before looking at the full results we set a line, that the gap to the control group be at most 20% of the effect. For financial assets the gap is 1.6% and 2.9% of the effect. For weekly hours it is 16% in Haiku and 34% in DeepSeek, which is above the line.

Other changes in the revision

  • Table 1 now reports the predicted holding rates, and Appendix B.18 gives them for each of the seven LLM families.
  • New Appendix B.19 compares type sampling with asking the LLM for probabilities, on holdings and on amounts.
  • Appendix B.11 adds a comparison of one, five and fifty types per household (Table B11b).
  • Section 5 corrects our statement of the first limitation, on the dispersion of simulated answers (Appendix B.15).
  • The related work in the introduction discusses Li et al. (2025).
  • Section 4 corrects three statements. The second criterion is judged on reported wealth in three LLM families (Appendix E.4), the comparison with Swedish lottery winners is removed, and in Kimi the share of the prize held as financial assets does not rise between the two larger prizes (Appendix E.9).

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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