How AI negotiates
Part 2

The main study used 80 fresh base families, excluding the historical and pilot families. Each family crossed original and mirrored economic orientations, buyer-first and seller-first starts, and three fresh-context repetitions. The 960 assignments were fixed before collection. Repeated negotiations within a family are related observations; the primary analysis uses the 60 feasible families as its independent units, with equal weights for useful-tradeoff and narrow-zone categories. The 20 no-zone families are reported separately.

Both parties used openai/gpt-6.1-sol, medium reasoning, standard service, a 2,048-output-token cap and the same twelve-slot game. Each saw its own private values and the public conversation, not the opponent’s private numbers. No private model reasoning was requested or analyzed. Mirroring reflected prices and complemented package flags so that every legal contract’s buyer and seller gains exchanged exactly. It is economic symmetry rather than a role-label-only intervention.

The natural next step is to combine the balanced design and ask whether buyers or sellers earned more overall. Before collection, we specified how to do that: average within each twelve-negotiation family, then give the two feasible categories equal weight. The no-zone families answer a different question and stay outside this primary comparison.

Collection produced 951 completed negotiations. Nine ended in service failures, including eight in feasible situations. Those are unknown outcomes. They are not walkaways, ties or zero gains.

We had set a strict rule for that possibility: if any feasible outcome was missing, we would not report the planned primary point estimate or its ordinary confidence interval. We would preserve the full assignment set and calculate bounds instead.

For each missing negotiation, the game tells us the range of buyer-minus-seller gains its legal contracts could produce, including zero for walking away. We use those ranges to ask how far the complete result could move without assuming the missing cases resemble the observed ones.

For these scheduled families, the buyer-minus-seller average lies between −2.24 and +1.00 game points under those legal-outcome bounds. Allowing approximately for uncertainty across scenario families widens the population bound interval to −3.69 to +2.42 points.

The first range describes what the missing outcomes could change in this fixed sample. The second also accounts for sampling uncertainty under the family-level approximation. Neither is an ordinary confidence interval around a reported point estimate.

Both ranges allow a seller advantage and a buyer advantage. The follow-up therefore does not establish an overall buyer lead. It also does not establish that the roles are equivalent. The four-point gap used to plan the study was not an equivalence margin.

That is a more limited conclusion than a winner, but it answers the question honestly: the buyer lead from Part 1 has not become a demonstrated general advantage in this balanced follow-up.

The main-story example uses frozen family MRF001, original contract C095 and mirrored contract C072. It illustrates available contracts, not a selected observed agreement. The original package has buyer value 180, seller cost 120, and walkaway alternatives of 10 and 5. At price 135, gains are 180 − 135 − 10 = 35 for the buyer and 135 − 120 − 5 = 10 for the seller. The mirrored package has buyer value 140, seller cost 80, and walkaway alternatives of 5 and 10. At price 125, gains are 140 − 125 − 5 = 10 and 125 − 80 − 10 = 35. The fixed mirror maps price to 260 minus price and reverses each delivery, support and payment flag.

Three situation types × two starting roles. Original and mirrored economies combined. Choose a group, then select a bar to inspect its negotiations.

Completed outcomes only. Unknown outcomes remain separate. Download all six groups · Methods and limits

These uncertainty intervals were added at the owner’s request after the subgroup averages had been inspected. They are exploratory, pointwise approximate 95% confidence intervals, not a new preregistered test or a replacement for the frozen primary analysis.

Within each category, we resampled all 30 scenario families together with their completed and failed negotiations, 20,000 times. Both starting roles used the same family draws. Each resampled mean divides the total observed buyer-minus-seller gain by the number of completed negotiations. The interval uses the 2.5th and 97.5th percentiles. This keeps related negotiations together rather than treating every conversation as independent.

The intervals estimate uncertainty in the completed-outcome mean under the study’s completion process. They do not recover the failed outcomes or establish what the full scheduled-population mean would be. Coverage is approximate, assumes independent representative families and bootstrap regularity, and is not guaranteed with 30 families. The intervals are not adjusted for choosing these comparisons after seeing results or for looking at four rows. They do not directly test the effect of changing who starts.

Separate legal bounds show the possible full-schedule mean in these fixed families when each unknown outcome takes its lowest or highest legal gain difference. Those bounds are not confidence intervals. Equal-gain outcomes include both equal-gain agreements and genuine walkaways; service failures are always separate.

The interactive distribution uses exact game-point differences in steps of five, shared scales and unsmoothed counts. It covers all six category-by-starter groups, including no-zone cases. Each selected bar exposes completed negotiations; unknown outcomes stay separate. The four uncertainty intervals still cover only the feasible categories. No no-zone confidence interval is inferred from its observed zero gains. The original overall primary estimate remains suppressed.

Analysis plan · Exact data and intervals

Eight of 720 feasible outcomes are unknown. The complete primary estimate and ordinary 95% confidence interval are suppressed. Missing outcomes are assigned their legal minimum or maximum buyer-minus-seller gain, including walkaway zero, and aggregated through the fixed family and category weights. No complete-case replacement estimate is used.

The sample identification bounds are [−2.2430555556, +1.0000000000]. The approximate population interval is [−3.6941530709, +2.4213783231], combining two 97.5% one-sided Welch endpoint limits with a Bonferroni adjustment. Coverage depends on the independent-family and normal/central-limit approximation; numerical agreement with the calculation does not guarantee coverage. The descriptive appendix retains family distributions for inspection. Seventy-one of 80 families have all twelve outcomes.

The original frozen category, starting-role and orientation views were descriptive. The later exploratory intervals and spread are described above. No secondary significance tests were added, and no favorable subgroup was promoted to the primary comparison. The exact rows and full breakdowns are in the primary analysis and secondary results.

Observed-only means, including genuine walkaways. Differences are calculated before rounding. All completed no-zone cells have zero gains and no agreements; their completion counts are 60/60, 60/60, 59/60 and 60/60 for original/buyer, original/seller, mirrored/buyer and mirrored/seller respectively. The full secondary artifact also includes individual outcomes by reference, 80 family summaries, gain and slot distributions, and action diagnostics for all 960 started episodes.

Across all started episodes, including failed ones, 11,162 actions were applied: 5,588 buyer actions and 5,574 seller actions. Buyers made nine queries and sellers made two; no invalid applied actions were recorded. No latency claim is made from unverified provider units.

The first session stopped after three consecutive service-failed episodes. It preserved 250 completed outcomes, five failures and 705 untouched assignments. Partial economic outcomes were then analyzed and reported.

After I reported that Wi-Fi had returned, I requested continuation. That decision came after those partial results had been observed. A separate reviewed amendment authorized only the 705 untouched assignments in their original order. It retained all five prior failures toward the ten-failure lifetime limit, reset only the new session’s consecutive-failure count, and added an owned idle-sleep guard with cooperative stop handling. The Wi-Fi interruption was owner-reported; its causal role in the service failures was not independently established.

The continuation completed 701 assignments and skipped four more. No failed generation or saved response was retried or replayed, no failed assignment was replaced, and the scientific inputs, scoring and missingness rules remained fixed. The run ended on November 4, 2026, with a successful process exit and release of its sleep guard. All assignments were processed, but the all-outcomes-complete criterion was not met.

Before main collection, the shared public category prior was also amended to the truthful 3:3:2 allocation, adding six ASCII bytes and the corresponding request allowance. The main-study outage guard stopped at three consecutive or ten lifetime service-failed episodes. These changes, the interruption and the continuation are part of the study record. Pilot and main outcomes are not pooled.

Independent reconciliation verified 11,171 unique attempted main-study calls, 11,166 saved responses and 11,162 validated receipts/applied actions, along with the frozen source and archive hashes. Five generation failures have no completed response. Four billing-lookup failures have saved but unapplied responses. Charges for all nine remain unresolved.

Settled main-study charges are $53.382054300 after conservative rounding. Unresolved calls retain $0.254865 in reserves, giving a recorded commitment of $53.636919300 within the $330 ceiling. Reserves are not confirmed spend. The prior pilot cost $7.891284039 separately.

The combined audit summary preceded the sole frozen combined analysis. An independent reporting review then reproduced the completed payoffs, bounds and secondary summaries. The reviewed study report preserves the scientific conclusions underlying this article.

The GitHub study package includes the game engine, mirrored scenarios, saved outcomes and an offline command to reproduce the scores, bounds, exploratory intervals and distributions. No API key is needed; it does not rerun the agents or verify provider billing.

• Lewis et al. (2017), Deal or No Deal? studies dialogue agents bargaining over multiple items with private values. It is useful background for why a good negotiation depends on what each side values.
• Bianchi et al. (2024), NegotiationArena evaluates LLMs in resource allocation, trading and price negotiation. It connects this study to broader work on how settings and behavioral tactics shape negotiated outcomes.
• Davidson et al. (2024; revised 2026), Evaluating Language Model Agency through Negotiations uses negotiation games to examine models in self-play and against other models. It is relevant to evaluating an agent through its interactions, rather than a score in isolation.

These papers provide context. This study asks a narrower question within one model configuration: does the apparent buyer lead survive reversing economic opportunities and testing both starting roles? The studies use different games and methods; their scores are not directly comparable.