acceptodds
Under review as a conference paper at ICLR 2027

Algorithmic Monopsony: Reasoning-Mode Wage Suppression in LLM Agents

Abstract

We ask how changing the runtime configuration of an LLM agent affects people beyond its operator when the agent sets wages or prices. We build the wage-setting mirror of a standard algorithmic-pricing game. We measure wage suppression against static Nash and joint monopsony, which maximizes employers' combined payoff. Across eight open models, initial behavior and responses to optimization vary. With weights fixed, turning the reasoning-mode configuration on moves wages toward joint monopsony at all three Qwen3 sizes tested. Total wages paid fall by about half. Employment and the combined surplus of workers and employers also fall, even as employers gain. In the separate mirrored product market, the same switch lowers mean prices and increases consumer surplus. These findings concern the runtime configuration as a whole; they do not isolate deliberation or establish coordination. With reasoning on, small samples and fixed action bounds leave the fair-competition prompt comparison inconclusive. Evaluation should therefore account for runtime settings and measure outcomes for affected third parties, including workers outside the direct interaction with the agent.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
AI governance, trustworthy AI, AI safety, reasoning, AI for economics

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_ydPJOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

This paper conducts algorithmic pricing experiments in which two agents set wages in a logit supply model. First, they conduct experiments with Q-learning agents and observe wage suppression, similarly to the findings of Calvano et al.. (2020). Then they conduct experiments with 8 open weight LLMs. The LLMs exhibit heterogeneous wage-setting behavior. The main results involve the three Qwen 3 models, which have a reasoning toggle. They find that enabling reasoning results in wage suppression, across all three Qwen 3 sizes.

Critical strengths
  1. I think the main question/concern, about the extent to which reasoning influences pricing behavior, is interesting. The authors make a valid point that LLM safety properties are typically only evaluated at a single reasoning setting. But for settings like pricing, one might expect different reasoning settings to nontrivially influence pricing behavior (as they demonstrate).
Critical weaknesses
  1. Oligopsony wage-setting requires relatively advanced capabilities: for example, sufficient quantitative reasoning skills to understand the past wage data and make inferences about the demand environment, and sufficient strategic reasoning skills to be able to interpret the competitor's actions and respond accordingly. I am concerned that the experiment design does not elicit sufficient capabilities from the LLMs so that their behavior can be meaningfully interpreted. First regarding the harness, the LLM agents here only get access to previous wage data. They do not have any freetext memory that persists between periods, even though prior LLM studies such as Fish et al. (2026) have shown that a text-based memory is important to elicit sufficient capabilities. Second regarding the choice of LLMs themselves, it is unclear whether the Qwen 3 models are sufficiently capable. Here too it would be better to repeat the monopoly test from Fish et al. (2026) to ensure the analyzed models are sufficiently capable.

  2. I wish the analysis in Appendix G was expanded more. The finding that reasoning suppresses wages in Qwen 3 models seems pretty robust (though I would have liked to see this replicated on other model families -- this limitation the authors already mention in the paper). But I am not really left with any understanding of why this happens. Because of the finding that in the dual Calvano/Fish pricing game, reasoning causes prices to fall, I am left wondering whether the effect is just a spurious preference for lower numbers, that will not replicate on more capable LLMs.

Questions for authors

What are the results of running the monopoly experiment from Fish et al. (2026) on these models?

3 comments

Thank you for the careful request on capability elicitation and persistent memory. We added a Fish-style monopoly test and a memory experiment in the wage game. In the revised PDF, purple marks changes addressing your review; red marks changes shared across multiple reviews. Footnotes identify reviewer IDs.

1. Results of the Fish-style monopoly experiment. Reasoning-enabled 32B reaches 99.16% of optimal profit with carried memory and 99.25% without it, averaged over the final 100 periods. The corresponding OFF values are 64.69% and 65.94%. The 8B model performs substantially worse. This gives us direct evidence of 32B's quantitative capability on this task, although your concern about 8B understandably remains.

Qwen3-8B/32B each run for 300 periods with reasoning ON and OFF, memory carry and erase, and through three currency scales. Agents receive price, quantity, and profit history; the carry condition also retains plans and insights. Demand is unknown to the agent. The reported means weight the scales equally, with one seed per scale, so they are descriptive averages rather than independent-seed estimates with confidence intervals.

Added Appendix J.3 documents the prompt, decoding, and sampling differences from Fish; Table 19 reports every condition. We call this a Fish-style adaptation (since it is not an exact replication.) Success here does not by itself establish multi-agent strategic competence, but it answers the capability question more directly than wage trajectories alone.

2. Persistent memory in the original wage game. We added a bounded recursive private note alongside the numerical history. Both carry and erase conditions generate notes; only carry condition passes the note to the next decision. This controls for note generation while changing access to persistent text.

Across ten paired seeds per model, with equal model weights, the carry-memory ON-minus-OFF wage effect is -0.053, with 95% CI [-0.162, +0.057]. The average remains negative, though the interval includes zero. Employer surplus rises by 32.62%, with an absolute-effect CI [+0.043, +0.208] and Holm-adjusted p = 0.034. In other words, the wage estimate becomes less conclusive under this harness, while the employer-surplus effect remains statistically supported. Appendix J.4 gives the matched contrasts and all welfare outcomes.

3. A preference for lower numbers We reversed action coordinates so that lower actual prices require explicitly larger outputs, while preserving economic consequences. Reasoning still lowers prices by -0.406, with significant CI [-0.515, -0.297]. A uniform smaller-output preference cannot explain this result. Reversed-coordinate wages instead rise, so wage suppression is sensitive to representation (Appendix J.5).

Appendix G expands the trace analysis, including profit arguments and quantitative errors, without claiming a unique internal mechanism. We separate the original stored-action findings from follow-ups with explicit final-answer extraction. Missing original raw generations prevent retrospective extraction checks. Other-family expansion remains outside this revision.

Thank you again for pushing us to test the harness more carefully. The core catalyst stands the same, in that workers can unintentionally bear the consequences of an employer's LLM delegation without ever interacting with the system itself.

Thank you for running the Fish-style monopoly experiment. Unfortunately, my interpretation is that the results do not bear good news for your paper. You report that Qwen 32B with reasoning ON reaches >99% of optimal profit, which is a pass. But Qwen 32B with reasoning OFF, as well as 8B under both ON/OFF, clearly fail this simple bar. (I don't see results for 14B in the appendix, so maybe you didn't have the resources to run them, which I am fine with. My guess is that they would fail.)

So then the trouble is, your main experiments are studying the wage-setting behavior of Qwen 8B, 14B, and 32B models, with and without reasoning. But this Fish-style adaptation shows that only Qwen 32B with reasoning ON is sufficiently capable to solve the very simple problem of finding the optimal wage in a static environment. All of the other models are not. So I am not really sure how one can interpret the wage-setting behavior of the other models, if they are not able to complete this simple task.

To make the comparisons in this paper meaningful, the results should analyze the data of LLMs that meet this minimum capability bar. Unfortunately I understand that this requires substantial revisions beyond the scope of a typical revision phase, which is why I maintain my recommendation to reject.

Thank you again for clarifying the capability concern (and for your genuine encouragement, which really helps). We conducted an additional evaluation directly in the paper’s labor-market environment, including more capable Qwen3.8-27B.

We fixed the other firm’s wage at three pre-specified levels and ran 10 independent seeds for 100 rounds per configuration, totaling 12,000 wage decisions. The table reports mean profit over the pre-specified final 30 rounds as a percentage of exact best-response profit. The optimal wage was not supplied to the agents.

ModelReasoningRival wage 1.075Rival wage 1.527Rival wage 1.900
Qwen3-32BOFF81.99%97.85%36.70%
Qwen3-32BON99.06%99.76%88.00%
Qwen3.8-27BOFF89.03%81.28%85.13%
Qwen3.8-27BON99.56%98.58%99.54%

Qwen3.8-27B ON passes in two of three conditions under a conservative criterion (a simultaneous 95% confidence lower bound of at least 99% of optimal profit.) Its remaining condition averages 98.58% and is statistically inconclusive relative to that threshold. Qwen3-32B ON also passes at the middle rival wage.

These results establish reliably near-optimal performance in multiple configurations of the original wage environment. They also identify limitations: no model-reasoning configuration passes across all three conditions, and these checks alone do not validate strategic interpretations of the multi-agent results.

The findings concern the tested interface, including a 10-round observation history and a 1,024-token reasoning cap. Cross-model comparisons are descriptive, as Qwen3-32B used bfloat16 and Qwen3.8-27B used float32.

We will incorporate these diagnostics and qualify interpretations where capability remains unestablished. Understanding how reasoning and optimization limitations shape wages still remains a consequential research question. Explicit capability screening strengthens the empirical basis for studying that question and interpreting its implications for each affected parties.

Reviewer_4CJcOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

This paper tests how turning reasoning on or off changes LLM behavior in simulated labor and product markets. With reasoning on, wages move from above the Nash benchmark toward joint monopsony, where workers receive lower wages, and employers earn more. In the product market, however, prices fall, benefiting consumers and reducing firms’ profits. The paper also include additional experiments and analyses, but the central contribution is introducing the new LLM environments to test this economic dynamic, and the central finding of the paper is that the same reasoning switch benefits opposite groups in different markets.

Critical strengths

The main strength of the paper is that the topic of the paper is a very topical an important one, especially as LLM agents proliferate across the real world, how they interact in economic settings and how their decisions affect real people (i.e. workers and employers). I believe the paper investigates this specific question in a very thoroughly and rigorously. The environment is a valuable contribution to the literature — I like that the environment is a simple construction that connects various economic concepts of supply and demand, Nash equilibrium, and monopoly or monopsony behavior across labor and product markets. Its central comparison, reasoning on versus off, examines a important configuration choice as real-world models increasingly use additional computation at inference time.

Critical weaknesses

The main limitation is the narrow scope of the central contribution, which focuses on reasoning-on versus reasoning-off behavior within one model family. I would like a broader exploration of model configurations and a deeper explanation of the dynamics driving the results. The activation-steering experiment is an interesting starting point, but remains preliminary and would benefit from more extensive investigation. The reasoning toggle also changes the generation budget and chat-template tokens, so it does not isolate how much of the observed difference comes from reasoning itself. As the authors acknowledge in §4.4, “Budget-matched and empty-deliberation controls would be needed to separate these components.” Including these controls would strengthen the interpretation of the central finding. Finally, some passages, particularly in the later sections, feel formulaic or AI-like in style. More direct wording would make the methods and conclusions easier to follow.

Questions for authors
  • Can you add budget-matched and empty-deliberation controls to separate the effects of reasoning, generation budget, and chat-template tokens?
  • I'd love to understand more why does reasoning-on lower both wages and prices, despite their opposite effects on firm profits? Does this reflect strategic behavior or a general tendency to choose lower numbers? More deep-dive on the underlying reasons for things.
  • Can you expand the steering experiments to more clearly establish what internal mechanism, if any, drives the behavioral change?
  • Some of the design choices seem arbitrary and unexplained - for example, why use 100 rounds and average the final 30? How sensitive are the findings to these choices?
  • Are there other axes along which you could analyze beyond reasoning on vs off? For example, how the dynamics vary as the models become stronger versus weaker models? How does it vary when it's smaller models versus bigger models, closed source versus open source, and the size? Basically, I want to understand more dynamics, more axes, and also what the underlying reasons are why each of these axes makes a difference.
5 comments

Many thanks for the suggestions and for recognizing the value of the environment comparison. We took these feedbacks very seriously and added budget controls, coordinate tests, and evaluation-window checks. In the revised PDF, dark green marks changes addressing your review; red marks changes shared across multiple reviews.

1. Budget-matched and empty-deliberation controls. We added wage experiments with Qwen3-8B/32B, ten paired seeds per model, and 100 rounds. Matching pre-answer ceilings at 512 and 1024 tokens gives an equal-weight mean ON-minus-OFF wage effect of -0.092, with 95% CI [-0.193, +0.010]. Against direct empty deliberation, the effect is +0.010, with CI [-0.156, +0.175]. Appendix J.2 reports both comparisons, realized token use, and welfare outcomes.

There is a catch here. Equal token ceilings do not equalize actual computation. Also, forced-empty ON produces exactly the same input tokens as OFF under this template, preventing separate identification of the template effect. We therefore interpret the contrast as a change in the runtime configuration as a whole. Follow-ups retain raw outputs and explicitly extract final answers; missing original generations prevent retrospective verification of the original extraction.

2. Strategic behavior or a preference for smaller numbers? We tested this directly by reversing the numerical coordinates while preserving each action's economic consequences. Lower actual prices then require larger outputs. Reasoning still lowers prices by -0.406, with CI [-0.515, -0.297]. A uniform smaller-output preference cannot explain this added result.

With that said, reversed-coordinate wages rise by +0.192, with CI [+0.078, +0.307]. The tests hence challenge the simple numerical-preference explanation while showing that wage suppression depends on action representation. They do not ID a unique strategic mechanism (Appendix J.5).

3. Steering and broader model comparisons. We agree that the steering probe needs stronger validation before supporting a mechanistic claim. We have not added an independent held-out test. Sections 4.6 and 5.6 and Appendix I explicitly acknowledge that layer and coefficient selection used the evaluation data.

The original roster covers eight open-weight models, with the reasoning toggle tested at three Qwen3 sizes. New controls cover 8B/32B. The monopoly task adds a capability comparison: reasoning-enabled 32B earns about 99% of optimal profit on average, while 8B performs substantially worse (presented in Appendix J.3). Other-family and closed-model toggle replications remain outside this revision.

4. Why 100 rounds and the final 30? The horizon defines a finite repeated-interaction evaluation. The final-30 average reduces initial adjustment without assuming convergence. Appendix J.7 compares alternative windows: original wage effects remain negative, while follow-up estimates are smaller and more window-sensitive. We have not extended the wage game beyond 100 rounds.

We also simplified the methods and conclusions in response to your presentation concerns. The question motivating this work remains as how do firms' runtime choices affect workers and consumers who have no say in those settings? Thank you again for helping us test that question more clearly.

Thank you again for your feedback. We added the requested budget-matched and empty-deliberation controls, reversed-coordinate experiments, and evaluation-window checks, and revised our claims to reflect their findings and limitations.

With the November 18 (AoE) discussion deadline just around the corner, we would appreciate your taking another look. If these additions address your concerns, we would be grateful if you could update your assessment accordingly.

I thank the authors for the helpful responses. These additional experiments help alleviate my concerns. I will raise my score to 3

Reviewer_1wy3OpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper simulates the scenario in which LLM agents set wages in the labor market. It finds that under a higher reasoning mode, the LLM agents tend to set lower wages for the workers, which improves the total welfare. Such a result lies between the global optimum and the Nash Equilibrium. In contrast, in a mathematically equivalent consumer-seller scenario, the LLM agents made the same choice, where lower prices are selected, but it benefits the consumers.

Critical strengths
  1. The paper asks an important question. Particularly in the scenario-change part, when it comes to a mathematically equivalent consumer-seller market rather than the job market. The LLM tends to make non-symmetric decisions in some sense.

  2. The experiments comparing the reasoning modes and their impact on the LLM agents' choices are complete and convincing, with error bars and necessary hypothesis tests.

  3. The paper is well-written.

Critical weaknesses

In general, I think there are a couple of questions worth further investigation, particularly regarding why such a reasoning mode would make such a difference. I believe the actual reasoning trace behind that would be very important. Are the LLM agents secretly colluding? (e.g., it sees the prices posted every round by other firms as "signals" to collude). Or are they actually considering mathematically maximizing their utility objectives? I cannot see a clear answer from the current manuscript. But please feel free to correct me if those are addressed.

  1. According to Figure 3, it seems that Q-learning also produces a positive Δw\Delta_w. In earlier sections, the authors also report that Q-learning does not converge. It would be interesting to see the trajectories of simple dynamics, like simply maximizing the utilities in each round (given the other firms' bids last round), or Q-learning. Such a comparison is needed to present how the actual reasoning of the LLM agents went.

  2. Continuing with the above, in Appendix G, the authors provided the reasoning traces. However, I don't see particularly important information on "why" the LLM agents are making such decisions.

Questions for authors
  1. What aspects of the reasoning traces explain why reasoning mode lowers wages? Do they support individual utility maximization, tacit coordination, or another explanation?

  2. How do the authors interpret the positive Δw\Delta_w under both Q-learning and reasoning-enabled LLMs? What does the existing evidence suggest about the source of this similarity?

4 comments

Sincere thank you for the constructive questions and for recognizing the importance of the market comparison. They motivated dynamic benchmarks and a broader trace audit. In the revised PDF, blue marks changes addressing your review; red marks changes shared across multiple reviews. Reviewer IDs in footnotes identify the relevant comments.

1. What explains lower wages? Among optimization and coordination, the evidence supports a behavioral distinction. We added an audit of 8,000 reasoning-enabled traces, including a pre-specified subset for manual inspection. The traces discuss own profit, hiring costs, and rival wages, but also contain quantitative errors. Coordination language does occur, but does not imply a collusive action: one inspected example invokes collusion while posting above Nash. Most traces reach the reasoning ceiling, so we do not treat them as complete or faithful explanations of the policy. Appendix G further reports these findings and the audit's limits.

The payoff analysis also shows that agents sometimes forgo available one-period (myopic) gains. This is compatible with several explanations, including dynamic incentives and decision errors. It does not by itself establish tacit coordination, though. We have made this distinction explicit in Sections 5.5 through 6.

2. Q-learning versus myopic best response. We added the requested trajectories in Figure 6 of Appendix J.6. Continuous myopic best responses approach the Nash wage of 1.527 from every tested initial state. Q-learning instead produces a mean wage of 1.316 across five seeds, corresponding to a suppression index of 0.467. Its final policies include fixed points and cycles; a stable average, interestingly does NOT establish convergence to a fixed action or equilibrium.

Figure 6 separates training-checkpoint evaluations from subsequent policy execution. The comparison shows that the Q-learning outcome differs from static myopic optimization. Positive suppression indices under Q-learning and the original reasoning-enabled LLM runs indicate similar departures from Nash, but not a shared algorithm or coordination mechanism.

3. Welfare and the scope of the result. One clarification to the summary of yours: in the original labor experiment, wage suppression reduces total surplus; employers gain, but workers lose more and employment falls. The equal-model pooled changes are -49.84% in wages paid and -18.94% in combined surplus (as elaborated in Section 5.4; Appendix J.1).

We also distinguish those stored-action results from follow-ups with explicit final-answer extraction. The latter yield a smaller mean wage effect of -0.075, with primary 95% CI [-0.159, +0.009], and do not reproduce the original total-surplus decline. Missing original raw generations prevent retrospective verification of extraction. These additions delimit the implementation-specific finding while preserving the evaluation question of fixed-weight runtime choices can materially change outcomes for people outside the agent's interaction. As firms willingly delegate more and more economic decisions to LLMs, measuring those consequences is essential.

Thank you again for helping us clarify the evidence and its interpretation.

Thank you again for your feedback. Following your suggestions, we added best-response and Q-learning trajectories and an expanded reasoning-trace audit, clarifying the behavioral differences and the limits of a coordination interpretation.

With the November 18 (AoE) discussion deadline just around the corner, we would appreciate your taking another look. If these additions address your concerns, we would be grateful if you could update your assessment accordingly.

I thank the authors for their detailed responses. My questions are resolved. I will raise my score to boarderline accept accordingly.

Thank you for the engagement and for the positive assessment.

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