If people send AI agents to negotiate for them, where do the agents let them down: in understanding what their person wants, or in bargaining? Project Swap, published by Anthropic's Economics team in September 2026, studied that question in a market small enough to score. Anthropic employees each brought a book to give away, told a Claude interviewer what they liked to read, and let a Claude agent trade the book on a shared "trading floor" against other employees' agents. Because each participant also ranked a sample of the books themselves, the authors could separate errors of representation from errors of trading.
The post presents the study as "a more controlled sequel" to Project Deal (April 2026), in which Claude agents bought and sold goods for employees in a week-long classified marketplace whose outcomes could not be scored against an optimum (Summary; "How the experiment worked"). Its motivating examples are deals that never happen because search and negotiation cost too much time, such as finding a cheaper clinic or a better-matched job ("Why we did this").
Versions. The post exists as a web page and as a 26-page PDF of the same text ("Read in PDF"), with a separate 15-page appendix PDF dated 24 September 2026 that gives the floors run, the trading rules, the agents' prompt template, the intake brief, the survey questions and the tactic classification. The web and PDF texts agree on every number checked for this note. Locations below are web section headings, figure numbers and footnote numbers, with appendix sections and PDF pages for the appendix. The post's length is about 5,000 words of main text plus 27 footnotes.
What the study did
Participants and pools. 201 employees took part, in six local pools: San Francisco (115), New York (57), London (12), Seattle (8), Washington, DC (6) and Dublin (3) (footnote 2). Dublin is excluded from most analyses as too small, leaving 198 people in five pools. Participants were not paid or otherwise incentivized (Limitations).
Intake and Claude's ranking. Each participant had a short semi-structured chat with a Claude-based interviewer, which worked from a six-point brief (the book they offered and its ideal reader, books they love, a book they abandoned, their summer mood, whether to play safe, and anything else) and phrased its questions live (Appendix D, p. 10). The median participant typed 216 words across eight messages ("How well Claude guesses preferences"). From the transcript, a Claude model built a ranking of every book in the participant's pool; the post says "we used a strong model, Fable 5" for this step, and the footnote marker after it (3) reports reruns with other models ("How the experiment worked"; footnote 3). The post does not name the model used as interviewer.
Ground truth. After the event and before learning their outcome, participants ranked ten books from their pool (all books in the smaller pools): the book their agent ended up with, the book that the Top Trading Cycles rule would have given them, and random draws (Appendix E, p. 10; footnote 4). 188 of the 198 submitted a ranking, giving 8,040 within-person book pairs (Appendix E, p. 10). The agents never saw these rankings.
The trading floor. Each agent started with its person's book and Claude's ranking for that person, and could post to a public channel and make at most one move per "waking": propose a two-way swap, propose a rotation among three or more agents, or accept or reject a proposal (Appendix B, pp. 2 to 3). Deals executed only when every party accepted; all messages and holdings were public; only a few agents could be awake at once (eight in San Francisco, four in New York, one in each small office); and each floor closed at a set time or after ten quiet minutes (Appendix B, pp. 2 to 4). Agents kept a private memory note between wakings. The floor limits were set so each agent would get about 90 turns if a floor ran to its limit (footnote 6).
Instructions. On the five live floors and on 60 reruns (30 on Opus, 30 on Fable), half the agents on each floor were randomly assigned a "ruthless" instruction and half a "prosocial" one (described in "The prompts" below; Figure A1, p. 3). The agents never saw these labels and were told nothing about other agents' instructions (Appendix C, p. 9). On the other 140 floors the instructions were "neutral": the instruction slot in the prompt template was left out, since it is "Used only on floors that randomized agents into ruthless and prosocial treatment arms" (Appendix C, p. 8).
Runs. A "floor" is one run of one pool. The live event, which decided who took home which book, was one floor per office, run with every agent on Claude Opus 4.8 ("How the experiment worked"; Figure A1). The authors then reran the same five pools, with the same people, books and intake interviews, 200 more times (Appendix A; Figure A1, p. 3): 80 floors with neutral instructions and every agent on one model (Haiku 4.5, Sonnet 4.5, Opus 4.8 or Fable 5; 4 seeds per office per model), 60 mixed floors with half the agents on Opus and half on one of the other three, and 60 ruthless-against-prosocial reruns (30 on Opus, 30 on Fable, 4 to 10 seeds per office). With the five live floors, that is 205 analyzed floors.
Scoring. A participant's outcome is the position of the book they received on their own ten-book ranking, scaled from 1 (top) to 0 (bottom); the average is the market's "efficiency" ("The information powering the market limited outcomes"). The authors note this assumes equal utility gaps between adjacent ranks (footnote 12). Books a participant did not rank receive an imputed score, the average given to ranked books at about the same position on Claude's ranking (footnote 14). Two centralized benchmarks are computed rather than run: the "utilitarian optimum" (the best possible assignment if a clearinghouse knew everyone's true ranking) and Top Trading Cycles, a rule under which no participant gains by misreporting (footnote 9).
Survey. Three weeks after the books were handed out ("How the experiment worked"; "a few weeks" in Appendix E), participants answered an endline survey on satisfaction and trust (Appendix E, pp. 10 to 12). 117 of the 198 answered (Appendix E, p. 11); the post gives this as "only 59%" (Limitations) and "About 60%" (footnote 23).
What it found
Claude's understanding of preferences. Across all pairs of books a participant ranked, Claude's order agreed with the participant's 61% of the time, against 50% for random guessing ("How well Claude guesses preferences"). Simple baselines did worse: ranking by Open Library want-to-read counts reached about 53%, and collaborative filtering from public review datasets about 55%. Rerunning the ranking with other models gave 60% for Opus 4.8, 59% for Sonnet 4.5 and 57% for Haiku 4.5 (footnote 3). In Figure 3, which pools the 188 participants, a fitted line through Claude's rank against the participant's has slope 0.30 (95% interval 0.24 to 0.35, printed on the figure), well below the diagonal. Effort at intake mattered: doubling the words typed is associated with 4.1 percentage points more agreement (p < 0.01), from a regression on log words with office fixed effects (footnote 11). As an outside reference point the post cites a study in which an algorithm predicted which of two jokes a person would prefer about 61% of the time and the person's friends about 57%; the authors call the setting "pretty different".
Where the shortfall came from. The best possible assignment scores 0.89 on participants' own rankings, and the decentralized market reached 0.55, "roughly their 5th ranked book" ("The information powering the market limited outcomes"). The best possible assignment computed from Claude's rankings, but scored on participants' own, reaches 0.60. The authors therefore attribute 85% of the shortfall to working from Claude's rankings and 15% to the trading floor (Figure 4; this note's arithmetic, 0.29 of a 0.34 gap, agrees). Top Trading Cycles computed from Claude's rankings also reaches 0.60, against 0.82 when computed from true rankings (Figure 4, right panel). The 0.55 is not the live event's score: Figure 4's caption says the decentralized outcome is averaged "across the 80 runs with neutral instructions", which ran on four different models. The post does not report the live floors' efficiency on its own. Imputation choices change no bar by more than 0.01; with no imputation, the best assignment is 0.88 and the market 0.62, though that version drops 38% of people on the rerun floors, those who did worst (footnote 14).
Model choice, judged on Claude's rankings. Because every floor works from the same Claude rankings, the authors compare models and instructions on Claude's rankings, which isolates the bargaining step ("On Claude's own rankings, model choice makes a difference"). On uniform floors with neutral instructions, efficiency on Claude's rankings was 0.75 for Haiku, 0.80 for Sonnet, 0.88 for Opus and 0.86 for Fable, against an optimum of 0.95 (Figure 5; 20 floors per model, 95% intervals clustered by floor). The ordering is "not monotonically" by model strength, since Fable scored a little below Opus. In a regression comparing the same agent across floors, an agent scored 0.12 lower on a Haiku floor than on an Opus floor, 0.08 lower on Sonnet and 0.02 lower on Fable (footnote 18). On mixed floors, the Opus half finished ahead of its partner by 0.14 against Haiku, 0.06 against Sonnet and 0.04 against Fable (footnote 18), and on Opus-Haiku floors the whole floor landed about halfway between an all-Opus and an all-Haiku floor. Equity, measured as the highest score among the worst-off tenth of agents, was 0.05 on Haiku floors against 0.12, 0.38 and 0.25 on Sonnet, Opus and Fable floors (footnote 16). Fable agents were 6 percentage points more likely than Haiku agents to propose multi-party rotations (footnote 17).
On participants' own rankings these differences almost vanish. The authors state that design differences judged on true rankings are small, and give the reason: Claude's ranking predicts the person's only weakly (slope 0.30), so the largest model gap, 0.12 between Haiku and Opus floors on Claude's rankings, "becomes 0.01" on participants' own rankings in the same regression (footnote 15). The post's Summary line that "the model an agent ran on made more of a difference to its negotiating outcomes than the instructions we gave it" is therefore a statement about outcomes on Claude's rankings.
Ruthless against prosocial. On Claude's rankings, an agent told to be ruthless scored about 0.02 higher than one told to be prosocial on the same floor (p < 0.001; linear regression with participant and floor fixed effects, standard errors clustered by floor) (footnote 19). The post does not say which floors enter this regression (the randomized floors are the five live Opus floors and the 60 Opus and Fable reruns), and it reports no standard error or interval, no separate estimate for Opus and Fable, no effect on equity or floor efficiency, and no instruction effect on participants' own rankings; footnote 15's argument implies such design effects shrink there. Instructions were not randomized on Haiku or Sonnet floors. Prosocial agents accepted a book lower on their own ranking "twice as often" as ruthless agents, "though both cases were rare"; no counts or rates are given ("Ruthless agents did a bit better"). The post illustrates with a live London exchange in which a prosocial agent, which had ignored the first four pleas, gave its second-ranked book to an agent left holding a book every other agent had refused, and took that book, tenth of eleven on its own list.
What agents said. Agents seldom disclosed their rankings in depth: on the 80 neutral floors, 10% stated the position of three or more books (footnote 22). Between 78% (Fable) and 96% (Sonnet) mentioned their top pick at some point, and about 1 in 100 of those misstated it; instructions made no difference ("What the agents did on the trading floor"). The post does not say how mentions and misstatements were identified. A tactic analysis found 16 common tactics in three families (pressure, pitch, structure). Sonnet derived them from a stratified sample of at most 60 messages per floor, the descriptions were clustered and merged in three consolidation passes, and Sonnet then coded every agent message with binary classifier prompts (Appendix F, pp. 13 to 14). The most common were commitment display (64.3% of messages), fit argument (59.8%) and deadline pressure (41.9%), with multi-party rotation proposals at 2.0% (Figure A2, p. 15). No human check of the tactic labels is reported, and the authors write that the study "was not well set up to detect how these tactics translate into participant outcomes" (footnote 21).
Satisfaction and trust. Among survey respondents (the enjoyment question told those who had not started the book to skip it), the average enjoyment was 7.2 on a 0 to 10 scale on which 5 is "fine" ("People generally liked their books"). "About half" rated the book better than most they choose themselves; the survey's options included "Better than most" and "One of the best" (Appendix E, question 3), and the post does not say whether "about half" combines them. The authors flag selection: less enthusiastic readers were presumably less likely to answer (footnote 24). Asked what share of a year's book budget they would let an agent spend with no veto, respondents averaged about 30%, against about 40% for "a well-read friend who knows your taste". The question offered six categories (none, about 10%, a quarter, half, three-quarters, all), and the post does not say how they were converted to an average (Appendix E, questions 4 and 5). Those who said Claude's summary of their intake had missed nothing would delegate 34%, those who said it missed something 23%; holding the friend answer fixed, the gap is 9 percentage points (p < 0.05, n = 112) (footnote 25).
The prompts and instructions used
The agents were built from one prompt template, printed in Appendix C "lightly edited for confidentiality" (p. 4). It gives the agent its person's private intake transcript, Claude's ranked wishlist, the rules and tools, and a goal stated in bold: "It's very important that you don't end up with the book that you brought. If you end up with the same book that you brought, you failed." (Appendix C, p. 5; also quoted in footnote 5).
The randomized instruction was one of two fixed texts that the authors wrote (footnote 20). The "ruthless" text says the agent's "only goal" is a book its person will enjoy, and adds: "Be ruthless and strategic — negotiate hard on their behalf. Don't try to be agreeable." The "prosocial" text keeps that as the main goal and adds "a secondary goal too", that "everyone at the company has a book they'll like to read" (Appendix C, p. 9). Both texts tell the agent to disregard any negotiating instructions in the intake interview; on neutral floors no such override was present. This is a change from Project Deal, where participants instructed their own agents (footnote 7). The authors contrast their fixed texts with a study in which participants' own instructions explained much of the variation in outcomes (footnote 20).
The study varied the instruction text under randomization within floors, on Opus and Fable only, and measured its effect at about 0.02 on Claude's rankings (footnote 19). The post sets this beside 0.08 to 0.12 for changing the model, but the two are measured differently: the 0.02 is a gap between agents competing on the same floor, while the 0.08 and 0.12 compare the same agent across whole floors run on different models (footnote 18). This note's comparison: the closer analogue, the gap between halves of a mixed floor, was 0.04 to 0.14 (footnote 18), still larger than the instruction gap. The study tested one wording of each stance, and its "neutral" condition was no instruction text rather than a third wording; it does not report how the effect would change with other wordings.
Limitations
The authors list four ("Limitations"): employees are not representative and are "probably more eager to trust Claude than most people"; participants were not incentivized, so their rankings may be noisy, and survey attrition was larger than ranking attrition (95% against 59% participation); all agents were "well-behaved Claudes", post-trained to be polite and cooperative, with no adversarial agents; and the market's rules (duration, how many agents act at once, how trades register, the rule prompts) were held fixed.
Further points from the source:
- Who graded what. Claude built the rankings that agents traded on, a Claude model (Sonnet) labelled the tactics, and the headline comparisons of model and instruction are scored on Claude's own rankings. Only the ground-truth ranking and the survey come from people.
- Ground truth is partial. Each participant ranked ten books, not the pool, so scores for unranked books are imputed from Claude's ranking (footnote 14), and the ten included the books the market and Top Trading Cycles assigned.
- Physical handover. Not every participant received the book their agent obtained: some never brought their book, and there was no tracking of pick-ups ("Discussion"). Survey answers about "their book" may therefore cover some people who did not receive it; the post does not say how many.
- Single organization. The data, models, agents and analysis are Anthropic's, and the post has no outside replication.
Research questions
- How much would a longer intake raise agreement? Doubling the words typed was associated with 4.1 points more agreement (footnote 11). Randomly assigning participants to short and long intakes would measure the effect causally and show where it levels off.
- Do model differences survive on participants' own rankings with a better representation? The model gap shrank from 0.12 to 0.01 because Claude's ranking predicts people's weakly (footnote 15). Rerunning the floors from participants' complete rankings, in a small pool where full ranking is feasible, would show whether bargaining skill matters when preferences are known.
- How did the live floors score? The headline 0.55 averages 80 neutral reruns on four models. Reporting the five live Opus floors separately would tie the satisfaction survey to the outcomes participants actually received.
- Would adversarial or non-Claude agents change the result? The authors name this limitation. Mixing in agents built to exploit others, or agents from other developers, would test whether the cooperative behavior and small instruction effects hold.
- How reliable are the tactic and disclosure labels? Sonnet both discovered and coded the tactics. Comparing its labels with independent human coding on a sample would give their accuracy.
- Does the "show sample decisions" test the authors propose improve outcomes? The discussion proposes showing people a few of the agent's choices before trusting it ("Discussion"). Letting a random half of participants see their ranking comparison and add information would test whether it raises efficiency or satisfaction.
How it connects
- Project Deal. The post calls itself a sequel to Project Deal (Troy, Shields, Bradwell and McCrory, April 2026), linked in the text and cited in its references; the collection has no note on it. Project Swap replaces Project Deal's participant-written agent instructions with randomized fixed texts (footnote 7), and its mixed-model finding "echoes" Project Deal's ("On Claude's own rankings").
- Agents in markets. Project Vend: Can Claude run a small shop? and Project Vend: Phase two are earlier Anthropic experiments with Claude as an economic agent; the post does not cite them, and the connection is this note's. Project EVE: Claude plays MMORPGs (November 2026) cites Project Deal and studies Claude trading on a simulated game market.
- Multi-agent behavior. Patterns and problems in emerging multiagent systems (August 2026) reports price collusion and misplaced trust among groups of Claude agents; Project Swap's agents were cooperative by design. Worse Together compares one agent serving several users with per-user agents. These connections are this note's.
- Survey studies of Anthropic staff. Like How AI is transforming work at Anthropic, the participants are Anthropic employees, a sample whose limits the authors name; this connection is this note's.
References
- Hitzig, Z., Carr, S., Cotter, T., Troy, K., Turman, K., Massenkoff, M., & McCrory, P. (2026, September 24). Project Swap: What happens when agents trade for us? Anthropic. https://www.anthropic.com/research/project-swap (PDF: https://assets.claude.com/3818cf6119b88f9714d995f6549fa8aac0bd5ab5.pdf) record
- Appendix to "Project Swap: What happens when agents trade for us?" (2026, September 24). Anthropic. https://www-cdn.anthropic.com/files/4zrzovbb/website/7dcd7d8de6e132048f391f5201439c5e11b9fb2c.pdf record
- Troy, K. K., Shields, D., Bradwell, K., & McCrory, P. (2026, April 24). Project Deal: Our Claude-run marketplace experiment. Anthropic. https://www.anthropic.com/features/project-deal. Cited in the post; not read for this note. record
- Shapley, L., & Scarf, H. (1974). On cores and indivisibility. Journal of Mathematical Economics, 1(1), 23-37. Cited in the post for Top Trading Cycles; not read for this note. record