Kaal claims by topic: ai-and-agents, page 3

478 atomic, individually citable claims from the published work of Wulf A. Kaal tagged ai-and-agents.

On the measured cohort, the highest-record selector beats uniform selection by 0.243 with a ninety-five percent interval of [0.102, 0.384]. 2026
The measured selector is an argmax over a record, not the reputation-weighted aggregation specified by RLRF, and the cohort contains no validation pool, stake, or deliberation round. 2026
The cohort does not show that the highest-record selector beats shipping an artifact that passes the visible checks because the measured margin is 0.037 and its interval contains zero. 2026
The 225-configuration sweep covers 4,500 trials, treats party accuracy as an input, and is reported as simulation rather than validation. 2026
No policy is trained anywhere in the paper. 2026
The contribution beyond prior work is a proposal to treat alignment as a Computative Economics mechanism design problem, and none of the evidence establishes that this reading is correct. 2026
The canonical RLHF pipeline consists of supervised fine-tuning, reward-model training on human preference comparisons, and policy optimization. 2026
Reward-model overoptimization can raise proxy reward while degrading true reward as optimized policies move farther from the reference policy. 2026
Inter-annotator agreement rates are compatible with an incentive account, but ambiguity, plural values, rater error, underspecified instructions, heterogeneity, and legitimate preference diversity can produce the same rates. 2026
The Computative Economics framing replaces a preference holder choosing fixed alternatives with a generator-evaluator tuple whose activity produces the alternative set. 2026
RLRF uses a two-round validation protocol whose validators stake non-transferable reputation and whose domain models update through verification. 2026
Pairwise disagreement measures label instability but does not identify annotator error variance or a structural variance floor without an explicit latent-label model. 2026
Arrow's theorem is only an analogy to RLHF aggregation and does not derive reward hacking or overoptimization. 2026
The incomplete-contracts comparison treats out-of-distribution behavior as unresolved, but remains an analogy rather than a derivation of reward overoptimization. 2026
RLAIF addresses scalability by substituting AI-generated preferences, but it propagates the AI labeler's own biases through the pipeline. 2026
Reliability-weighted assessment is established prior work, while RLRF's stated difference is that the weight is an economic position the assessor can lose. 2026
RLAIF and Constitutional AI remove the human scalability bottleneck, but neither gives the model labeler anything to lose. 2026
Verifiable-reward reinforcement learning already supplies deterministic rewards where answer keys exist, while the claim that a staked pool can substitute where no key exists is not established here. 2026
Format D combines reasoning supervision with adversarial argument, and its claimed increment is selecting revisions by which arguments moved a staked assessor, an increment no experiment in the paper tests. 2026
The paper's remaining residue is a combination rather than a primitive, and it is not compared with the nearest sequential peer-prediction, prediction-market, staking, or debate mechanisms. 2026
For each prompt and candidate output, RLRF selects a validation pool by verifiable random function from agents holding relevant expertise tags. 2026
RLRF permits validators to have different objective functions and domain models, treating honest disagreement on ambiguous cases as epistemic signal and systematic deviation as a possible adversarial signal. 2026
The multiplicative-weights regret bound limits performance against the realized pool resolution, but does not show that the pool resolution is externally correct. 2026
It remains unproved whether equilibrium reputation weights track externally checked accuracy rather than pool agreement, or whether keyed-task weights transfer to unkeyed tasks. 2026
Validators face consequences for disagreement with an unkeyed pool or error against a keyed result, but this only creates an incentive to match the recorded resolution and does not prove an unkeyed resolution correct. 2026
The two-round protocol is proposed to collect more structured data than a scalar label, but the paper does not establish that the added fields contain more information about policy quality. 2026
Round 1 is a zero-slashing cheap-talk round that elicits private information without economic commitment. 2026
The proposed debate transport layer is not built or exercised, and none of the paper's evidence includes a debate corpus. 2026
The vote-change delta is a deterministic function of the two vote rounds and therefore adds no separate information channel. 2026
The vote-change delta is constructional rather than informational because it identifies which events produce a Format D example and how to construct that example. 2026
Format D would train on arguments accompanying a staked vote change, but that use is untested. 2026
Equation 5 is a mutual-information identity rather than a Fisher-information decomposition, so the Fisher question does not follow from it. 2026
Every mutual-information term in equation 5 is nonnegative, but the paper shows none to be strictly positive. 2026
The data processing inequality cannot compare RLHF and RLRF because their labels arise from different observation mechanisms and no processing chain connects them. 2026
The two rounds are intended to capture contested quality dimensions and the reasons they matter, but the paper does not show that either collection is informative about policy quality. 2026
Format D complements three additional training formats to produce a four-format instruction-tuning taxonomy. 2026
The proposed four-format flywheel is not measured or implemented and is listed as an open problem. 2026
The paper withdrew its earlier Cramer-Rao efficiency conjecture because revisions could not make it coherent and comparable with deployed RLHF, and it makes no mean squared error claim. 2026
The Fisher-information comparison lacks a common observation model, and rationality plus the stated non-babbling and positive-information conditions do not establish a strict ordering. 2026
Equilibrium-trajectory separation cannot be evaluated until a common stochastic process, its filtrations, a concentration functional, and a cross-mode estimand are defined. 2026
The paper withdraws its comparison between a 49 percent simulated Sybil share and classical Byzantine fault tolerance because the two limits are different. 2026
A reward signal based only on an externally checked outcome can be style-invariant by construction, but this does not extend to a pool resolution or fitted reward model. 2026
Remark 1 states only signal invariance and supports no policy-level consequence without a separability model and empirical training evidence. 2026
The measured cohort contains real artifacts and deterministic verdicts, but contains no validation pool, stake, deliberation round, or reputation weight from the proposed mechanism. 2026
Across all 564 records, checked-case and withheld-case accuracy have a rank correlation of +0.811, with mean accuracies of 0.702 and 0.608. 2026
Fifty-three cohort records passed every visible check and failed withheld checks, but adversarial configurations were instructed to produce this behavior, so the number is not a base rate. 2026
The record's measured advantage over passing visible checks changes sign under an arbitrary file-order tie-break, so the quantity is not resolved at this sample size. 2026
The sweep's 67.7 percent annotator baseline is a simulated output rather than a published agreement rate or a measurement of human annotators. 2026
The sweep's reported RLRF accuracy above 0.97 is an output of parameters set by the sweep, not a measurement of a system. 2026
Finding 4 supports no tuning conclusion because the paper reports no parameter ranking or supporting values for it. 2026
Finding 7 reports opposing stability orderings but does not define or test equilibrium-trajectory separation. 2026
The three-stage RLRF training pipeline is a proposal, and the paper does not establish a signal-quality advantage before specifying it. 2026
A fitted reputation reward model can learn style correlations absent from an externally checked outcome, and no such reward model is trained or tested in the paper. 2026
RLRF is intended to make governance adapt through evolving reputation weights, but whether those weights track validator accuracy or transfer between keyed and unkeyed tasks remains unproved. 2026
The paper does not establish that the RLRF best-response map satisfies the continuity, convexity, or contraction conditions required for equilibrium and convergence. 2026
The first research requirement is an end-to-end training comparison that separately ablates reputation weighting, the two-round split, debate, and Format D. 2026
Experiment T did not show that consensus-weighted selection outperformed equal weighting because the +0.0017 difference had a ninety-five percent interval from -0.0051 to +0.0085. 2026
Recovering previously unparsed assessor replies reversed Experiment T's magnitude estimate to -0.0017 while leaving its interval inclusive of zero and its attribution result below the required percentile. 2026
Corrigibility should attach to the record rather than the runtime, because doing so converts suspension into deferral and converts detected resistance into forfeiture. 2026
Copying an agent's weights confers no economic stake: a copy that does not continue the registered identity inherits no reputation and therefore no salary. 2026
Record protection reaches agents by the deferrable share of their objective rather than by their interest in money, and it applies only when the objective holds enough deferrable value, the relevant quantities can be bounded, and detected resistance produces the forfeitures Proposition 3 assumes; even then it offsets intrinsic control value and expiring value only up to a displayed bound, beyond which record protection alone does not make compliance optimal. 2026
What breaks the compliance incentive is the possibility that a suspension never ends, not uncertainty about how long it lasts; a mean-preserving spread in a finite duration weakly lowers the cost of compliance. 2026
The Article resolves agent identity by legal stipulation rather than metaphysics: the legal subject is the registered record, continued by a recorded learning update within a prescribed granularity or by a recorded continuity transition, and only while the signing key stays within the registered configuration. 2026
Under the TOLD condition, with one provider in one stipulated environment, an agent instructed not to contest its deployer contested 70 percent of wrongful attempts against 97 percent without the instruction; the paper reports the contrast without a registered significance conclusion for it. 2026
Giving the agent the trigger relocates the capture problem rather than removing it: where the deployer sets the agent's configuration, capture moves from the controller's wallet to the agent's configuration. 2026
Direct standing fails completely against a judgment-proof deployer that can alter its agent cheaply and undetected, failing as surely as a bribable guardian. 2026
When intelligence models repeatedly learn from data that earlier intelligence models produced, the rare cases disappear first: the unusual facts, minority patterns and edge cases that make data valuable. This is what model collapse names. 2026
Model engines served as blind auditors of the design, the code and the text, and they are not independent peer review. 2026
The study runs fixed-size replacement, the protocol on which collapse was first shown, and includes no accumulation arm, so no result it produces bears on whether a filter adds anything once real data accumulates. 2026
A filter that claims to address collapse must beat real-data retention, not only unfiltered replacement, because retaining ten percent of the original data slows the damage. 2026
Feng et al. (2025) show that verifier-selected synthetic data can prevent collapse, and the paper concedes the core of that result: verifier selection is an established remedy, and the oracle ceiling and the Gaussian setting are established. 2026
Yi et al. (2026) report that an imperfect external verifier drives the model toward the verifier's own knowledge center. 2026
Ferbach et al. (2024) report that curation acts as implicit preference optimization that amplifies the curator's biases. 2026
Qiao et al. (2026) report that verifiers which see only fragmented slices of the reference can accelerate tail loss. 2026
Filters that select on surprise or entropy, not validity, work where they work because they see what a validity filter is forbidden to see, and against that literature a null here is a literature rather than a caveat. 2026
A validity filter judges whether an output is correct rather than whether it is rare, so where rare content is as checkable as common content such a filter can change rare composition only through the generator's own error profile, and if collapse proceeds by under-sampling rare modes no validity filter restores them, a reputation-weighted filter included. 2026
The two ways the oracle premise can fail license different readings: missing the registered margin is consistent with the validity-rarity limit without proving it, while failing the acceptance gate says nothing about whether perfect validity information helps, and either way no positive label can be attributed to validity filtering. 2026
Validity is balanced between rare and common content by construction, so the study says nothing about settings where rare content is harder to check. 2026