AI papers — 2026-08-25

Problem: General-purpose language models can reason and know facts but often fail at complex, long-horizon "working capability" tasks that require sustained interaction with files, search, and code, state maintenance, failure recovery, and verifiable delivery.

Method: Apodex 1.1 is trained along two scaling surfaces: Environment Scaling, which expands diverse, verifiable File, Search, and Code executable environments (each defined via a shared task contract E = (W, W0, q, A, T, Ω, B, D, VD)); and Agentic Coordination Scaling, realized through the Apodex Agent Team 1.1 (a lead agent that decomposes work onto an explicit persistent Task Board, dispatches on-demand subagents, supports asynchronous human intervention, asymmetric verification, adaptive "Max Team Effort," and an evidence-grounded synthesis stage). Both dimensions run on a shared execution harness with AgentOS as the persistent runtime (workspace state Wt = (Ft, Qt, Ct, It, Gt, Kt), /inputs–/workspace–/outputs namespaces, tiered context compaction, soft/hard budget deadlines, and controlled single-publisher artifact delivery). Training uses a unified SFT mixture (with model-soup merging across specialized SFT variants) followed by agentic RL using "PIVOT-RL," which applies hindsight-guided localized trajectory optimization at consequential "pivot" decision points, combined with asynchronous rollout optimization. The flagship model has 397B parameters; a 35B-parameter "Apodex 1.1 Mini" is also released for local deployment.

Key results: - APEX-Agents (professional work): Apodex 1.1 w/ Agent Team scores 38.5 vs. 16.5 for Apodex 1.0, and 34.4 with ReAct alone.

• GDPVal (win rate): Apodex 1.1 w/ Agent Team reaches 78.8 (vs. 69.5 with ReAct, a 9.3-point coordination gain), compared to 89.4 for Claude Opus 5.
• FrontierFinance: Agent Team reaches 54.3 (vs. 48.7 ReAct, a 5.6-point gain), the best score shown in that comparison table.
• FrontierScience-Research: Agent Team reaches 63.3% vs. 55.0% with ReAct and 28.3% for Apodex 1.0 (an 8.3-point coordination gain).
• BioMysteryBench (Human-difficult Set, 17 tasks): Agent Team scores 35.3% (6/17) vs. 23.5% (4/17) with ReAct, vs. 49.4% for Claude Opus 5.
• Humanity's Last Exam: Agent Team 56.1 vs. ReAct 53.2; DeepSearchQA: Agent Team 92.4 F1 vs. ReAct 88.2.
• Mathematics (MathArena protocol, Agent Team): IMO 2025 score rises from 12.5 (Apodex 1.0) to 36.5 (reference gold-medal threshold 35); IMO 2026 from 13.0 to 30.5 (threshold 29); USAMO 2026 from 5.8 to 26.5 (threshold 25); IMO-ProofBench Basic/Advanced reach 96.7%/63.3%.
• Coding: Terminal-Bench 2.1 score of 70.8; SWE-bench Verified score of 77.7.
• FrontierSearchBench (41 internal tasks): Agent Team achieves the best average score of 69.1 (87.8% positive, only 2.4% negative), ahead of GPT-5.6-Sol (67.4) and Claude Opus 5 (64.4).
• FrontierResearchBench (97 tasks, Pass Rate): Apodex 1.1 w/ Agent Team reaches 12.4%, below top systems like GPT-5.6-Sol/Codex and Grok-4.6/Claude Code (both 20.6%).
• Apodex 1.1 Mini (35B): on FrontierFinance/FrontierScience-Research/APEX-Agents, ReAct improves over Apodex 1.0 mini from 33.2→40.0 and 15.4→24.2 (APEX-Agents); Agent Team further raises Mini to 50.2, 51.7, and 27.7 respectively (gains of 10.2, 6.7, and 3.5 points).

Why it matters / caveats: The authors argue this demonstrates that broader executable environments plus trained agentic coordination can deliver frontier-band performance on complex work even from a comparatively smaller model (397B, and especially the 35B Mini), rather than requiring ever-larger parameter counts. However, they explicitly note limitations: on the hardest end-to-end scientific workflows (FrontierResearchBench), Apodex 1.1 still trails frontier systems and even the best system only passes 20.6% of tasks, showing reliable delivery of complete scientific workflows "remains challenging for all evaluated systems"; AgentOS's coordination/task-board state is run-scoped rather than a durable distributed database with atomic checkpointing; and the harness's runtime mechanisms guarantee state/execution/delivery contracts but do not by themselves guarantee that retrieved sources, computations, or conclusions are correct, so task-appropriate verification and human review remain necessary in high-stakes settings.

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Problem: Existing generative video and world models offer either passive prompt-based media or silent/action-restricted interactive rollouts, so there is no single system that lets a user continuously navigate a generated world in both first- and third-person perspectives while jointly receiving synchronized video, environmental sound, music, and speech.

Method: EchoWM organizes interaction around "camera intent," mapping discrete keyboard commands and continuous camera poses to a shared, dataset-level-calibrated relative 6-DoF trajectory, injected into the video backbone via a Unified Camera Positional Encoding (UCPE)-based relative camera-attention branch (zero-initialized output projection) that operates only on video tokens. Training uses a four-stage progressive curriculum: Audio-Visual Continued Pretraining (AV-CPT) on an AV-rich data mixture, Action Fine-Tuning (Action-SFT) that freezes the backbone and trains only the trajectory branch on a control-clean mixture, Joint Fine-Tuning (Joint-FT) that updates both parameter groups at a reduced learning rate on a balanced high-quality mixture, and Autoregressive Post-Training using audio-visual teacher forcing followed by short- and long-horizon Self-Gradient Forcing (SGF) with Distribution Matching Distillation (DMD) to produce a distilled four-step causal streaming variant, EchoWM-Flash. Training data comes from a custom "world data engine" combining internally collected gameplay, human-played Internet gameplay, Unreal Engine (UE) simulation, and general Internet video, with metric camera poses recovered via ViPE combined with VGGT-Omega and MoGe-2.

Key results: - On the 158-case WBench Navigation benchmark, EchoWM achieves the highest overall Average score (81.7), with a Consistency score of 89.8; the distilled EchoWM-Flash scores 81.0 Average and the highest Interaction score of 87.9, both ranking above all other listed baselines (e.g., HiDream-O1-World 80.9, Kling 3.0 79.0, Genie 3 73.9).

• On SANA-WM-Bench's 241-frame short-horizon evaluation, EchoWM achieves the highest VBench Overall on both Simple (83.91) and Hard (83.96) trajectory splits, with the lowest translation and CMC errors on the Simple split.
• Under the 961-frame long-horizon protocol, EchoWM attains VBench Overall of 81.36 (Simple split) with the highest revisit PSNR (15.10 dB); rotation error grows from 0.523° at 241 frames to 3.22° at 961 frames (Simple) and 12.05° (Hard), reflecting accumulated pose drift.
• EchoWM-Flash leads causal-model comparisons under the 961-frame protocol with VBench Overall of 80.13 (Simple) and 81.06 (Hard), plus the strongest trajectory accuracy and revisit consistency among evaluated causal methods.
• In a 200-case pairwise user study (World-Model Benchmark, WMB), EchoWM was preferred overall in 46.50% of judgments versus LingBot-World-v2 (LingBot-World-v2 preferred 21.57%) and 63.13% versus HappyOyster (HappyOyster preferred 27.06%).

Why it matters / caveats: EchoWM demonstrates that a single subject-agnostic camera-intent interface can unify first- and third-person navigation with native, synchronized multimodal (video, environmental sound, music, speech) generation across general and game domains without domain-specific controllers. The authors state explicit limitations: the model does not represent arbitrary actor intent (e.g., jumping, attacking, manipulation, robot commands) or implement game-engine rules/collision/deterministic transitions; it lacks explicit persistent 3D memory, so geometry, identity, world state, and audio can drift over repeated continuation turns; its interaction range is restricted to trajectories retained by the global scale filter, with generalization to substantially larger translations, higher speeds, or unusual rotations not established; and pose estimates from Internet/gameplay video remain imperfect even after filtering and may correlate with scene content or motion blur.

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Problem: Understanding e-commerce live streams requires jointly interpreting product facts scattered across noisy, temporally extended speech, video frames, product images, overlaid text, and user queries, a setting that existing omni-modal and e-commerce-oriented models are not primarily organized around.

Method: TLive-Omni builds on a Qwen3.5 backbone with the pretrained AuT audio encoder from Qwen3-Omni grafted in via a lightweight audio aligner, supporting up to 256K tokens of multimodal context. It introduces Per-vGrid, a timestamped token organization that groups each video grid with its temporally corresponding audio (derived from actual sampled frame indices) within explicit boundary tokens for precise audio-video temporal alignment. Training uses a three-stage SFT recipe (Stage 1: audio aligner only on 5M ASR samples; Stage 2: audio encoder + aligner on 26M ASR/caption/QA samples; Stage 3: joint multimodal SFT on 14M audio/image/video/text samples) built on a scenario-oriented atomic capability taxonomy and data engine, followed by Faithful-RFT, a GRPO-based reinforcement fine-tuning stage using task-conditioned, task-verifiable rewards (rule-based and LLM-judge) that scores final answers directly (suppressing explicit think traces) rather than rewarding reasoning-style rollouts. Training scalability is supported by a synchronized length-grouped sampler and a lightweight dynamic resampling strategy that regenerates near-zero-variance GRPO rollout groups. Two model sizes are released: TLive-Omni-4B and TLive-Omni-9B.

Key results: - Live-commerce ASR: TLive-Omni-9B achieves the lowest CER (6.46) among all compared models, and TLive-Omni-4B is close behind (6.66); both post among the lowest cpWER scores (12.27 and 12.88) for speaker-attributed ASR.

• Product visual grounding/text understanding: TLive-Omni-4B/9B achieve the highest Prod AP (91.45/89.96), text localization F1 (86.99/87.59), classification accuracy (79.06/79.85), and lowest recognition NED (4.72/4.24) among open-source and closed-source models compared.
• Video understanding: TLive-Omni-9B achieves the highest open-source results on temporal grounding mIoU (81.49), Video QA accuracy (93.23), dense caption accuracy (74.63), and lowest hallucination rate (8.76).
• General benchmarks: TLive-Omni improves over the Qwen3.5 4B/9B backbones on the majority of general benchmarks (e.g., MMBench 87.0/88.9, RealWorldQA 77.7/76.6) while achieving best open-source results on MLVU, Video-MME, LongVideoBench, and MMVU (9B) and on VideoMMMU (4B, 73.9).
• Omni-modal benchmarks: TLive-Omni-9B achieves the best open-source results on AVUT (80.0), WorldSense (56.0), DailyOmni (80.5), and FutureOmni (58.5).

Why it matters / caveats: The results indicate that aligning model design, data construction, training objectives, and evaluation with the target deployment scenario (live-commerce) yields strong domain performance without sacrificing general multimodal generalization. The authors state TLive-Omni remains focused on understanding rather than generation or full-duplex real-time interaction, and note future work is needed to extend evaluation on broader public benchmarks, improve robustness for longer/noisier/more diverse live-stream scenarios, and better calibrate temporal evidence under incomplete or ambiguous multimodal inputs.

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Problem: Instruction-based image editing frameworks that borrow the text-to-image training paradigm suffer from two discrepancies: insufficient attention to the granularity/diversity of edit concepts (datasets scale source-image diversity but not edit-concept diversity, causing distribution collapse) and training inefficiency from sparse supervision, since only localized regions are actively edited while most of the image is a static consistency constraint.

Method: The authors build a hierarchical taxonomy of 1,000+ fine-grained edit concepts and construct ConceptEdit-12M (12 million editing pairs) via an improved four-stage synthesis framework: (1) Library Construction, where an LLM iteratively expands a seed taxonomy (merge/prune, extrapolate subcategories, populate leaf nodes) refined by human experts; (2) Semantic Matching and Instruction Generation, where a VLM generator Φ matches concepts to source images and produces instructions plus instance-specific VQA verification criteria, with adaptive sampling weights to avoid distribution collapse; (3) Image Synthesis using models such as Flux.2, Qwen Image Edit, and Nano Banana2; and (4) Instance-Specific VQA Filtering with chain-of-thought (CoT) verification. They further propose "dense supervision via composition," using a VLM-driven aggregator Ψ to combine multiple spatially non-interfering edit concepts (disjoint regions, mi ∩ mj = ∅) into single composite image pairs, and release ConceptEdit-Bench, a benchmark spanning the 1,000+ categories. Base model for experiments is Z-Image, with instructions/filtering via Qwen3.5-122B-A10B and image synthesis via FLUX.2-klein-9B, trained with learning rate 1×10⁻⁵ and batch size 512.

Key results: - On ImgEdit-Bench, ConceptEdit1000 w/ Comp achieves overall scores of 3.48 (2M scale) and 3.75 (5M scale), beating ScaleEdit by +0.31 and +0.44 points respectively.

• Scaling edit concepts from 10 to 500 to 1,000+ categories raises ImgEdit-Bench 2M-scale scores from 3.05 to 3.26 to 3.33; at 5M scale ConceptEdit1000 (3.60) beats ConceptEdit10 (3.27) by 0.33 points.
• Dense supervision (w/ Comp) improves ImgEdit-Bench scores by 0.15 points on average across scales, and matching its performance without composite data requires 1.5× more training samples.
• On GEdit-Bench at 5M scale, GSC rises from 5.91 (English) / 5.83 (Chinese) at 10 concepts to 6.86 / 6.75 at 1,000 concepts, and dense supervision adds further ΔComp gains up to +0.45 (GSC, Chinese, 2M scale).
• Instance-specific VQA filtering outperforms generic validation by +9.0% Precision, +30.0% Recall, +21.0% F1-score, and +5.0% Accuracy (84.0/87.0/86.0/95.0% vs. 75.0/57.0/65.0/90.0%), against pseudo-labels from Gemini-3-Pro, while adding only +0.069s per-sample overhead.
• On ConceptEdit-Bench, closed-source Nano Banana 2 scores highest overall (66.19), open-source FireRed-Image-Edit-1.0 leads open models (65.86); nearly all models show notable declines in Portrait and Composition categories.

Why it matters / caveats: The authors state their dataset scale (12M pairs, 1,000+ subtasks) is the largest to date, tying with ScaleEdit-12M, and that ConceptEdit-Bench's fine-grained categories reveal model weaknesses (e.g., micro-expressions, spatial reasoning) that coarse aggregate benchmarks obscure; they also note their taxonomy deliberately permits moderate semantic overlap across categories (e.g., "neon lighting" spanning Style Transfer, Environmental Simulation, and Global Relighting) rather than enforcing strict mutual exclusion, and that the 1,000+ concept taxonomy targets daily, user-centric interactive editing rather than exhaustively covering specialized structural translation tasks.

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Problem: Existing mobile-agent benchmarks are either GUI-centric (testing only surface-level screen manipulation) or static function-calling benchmarks (offline string matching detached from real runtime constraints), so neither rigorously evaluates the tool-calling and long-horizon planning abilities of "mobile planner agents" that must orchestrate APIs, memory, skills, and sub-agents together.

Method: The paper introduces MobilePA-Bench, an interactive, stateful, tool-centric benchmark built on an executable sandbox with live application databases, 212 realistic mobile tools across 13 functional domains, and 1,705 real-world tasks. Tasks are organized around four capability dimensions—Basic Tool Use, Sub-agent Collaboration, Memory Usage, and Skill Usage—and each task is routed to one of three evidence-aligned "Query Buckets" (Bucket 1: Tool Call, Bucket 2: State Change, Bucket 3: Agent Behavior) with dedicated checkers plus capability-specific gates (e.g., a memory-retrieval gate requiring gold memory IDs, a gold-skill gate requiring the correct skill loader). The central planner interacts with the sandbox via a unified function-calling action space (direct mobile tools, sub-agent entry tools, memory tools, and skill-loading tools that dynamically expand the candidate action set), and an overall score is computed as a fixed weighted combination: 0.50×Basic + 0.10×SubAgent + 0.20×Memory + 0.20×Skill.

Key results: - Best model overall: Claude-Opus-5 at 75.52% weighted overall score; 7 of 13 evaluated models scored below 70%.

• Basic Tool Use ranged 68.94%–83.85% across models (13-model mean 76.58%), with Claude-Opus-5 leading at 872/1,040 tasks solved.
• Sub-agent Collaboration ranged 43.82%–77.53%, led by Gemini-3.1-Pro (77.53%) but that same model scored only 48.67% on Memory Usage.
• Memory Usage ranged 33.78%–64.63% (13-model mean 50.98%), led by Qwen-3.8-Max at 243/376 (64.63%), followed by Kimi-K3 (63.56%) and Gemini-3.6-Flash (62.77%).
• Skill Usage (pooled over Skill-Only Routing and Mixed Tool-Skill Routing, 400 scored trajectories per model) ranged with a 13-model mean of 66.77%; Claude-Opus-5 led at 312/400 (78.00%), followed by Kimi-K3 (76.50%) and Qwen-3.8-Max (76.25%).
• Stability check: three repeated runs of Qwen3.6-27B gave an Overall score range of only 57.22%–57.63% (std. 0.22 points), with the largest per-dimension spread in Sub-agent Collaboration (2.25 points, from just 2 differently resolved tasks out of 89).

Why it matters / caveats: The authors conclude that no single model dominates across all four dimensions (strongest results are split across Claude-Opus-5, Gemini-3.1-Pro, and Qwen-3.8-Max), and that errors cascade across capability boundaries in realistic multi-stage tasks, with models tending to issue premature or hallucinated tool calls instead of adapting to runtime feedback like PermissionDenied errors. Even the best model's 75.52% score and sub-65% memory performance indicate current frontier LLMs remain far from reliable for autonomous mobile deployment; the authors position the fully open-sourced benchmark and sandbox as a diagnostic tool and a foundation for future agentic reinforcement learning.

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Problem: Standard agent harnesses restrict a language model to a bounded sequential processor with only its weights and active context, so harness limitations (dropped state, restricted actions, miscounted resources, premature termination) can masquerade as model failures and prevent accurate measurement of a model's true long-horizon capability.

Method: Prime Agent is an open-source harness built on a four-level state hierarchy (L0 model weights, L1 active context, L2 persistent REPL and recursive subagents, L3 disk-backed history/memories/skills/prompts/subagent specs), each level updated by a distinct mechanism (fine-tuning, compaction, "agentic garbage collection," and "refinement," respectively). It implements the Recursive Language Model (RLM) abstraction via an asynchronous rlm primitive over a persistent IPython REPL for programmatic context processing and test-time compute, integrates "Continual Harness" for versioned, revisable prompts/memories/skills/subagent specs, supports direct agent-to-agent communication through daemon-mediated queues for multi-agent coordination, and exposes an "Agents View" for human inspection of daemon-backed sessions. Three long-horizon control mechanisms are defined: autonomous mode (turn-budgeted with an end-condition test), goals (persist until agentic completion), and heartbeats (cron/timed turns).

Key results: - On ARC-AGI-3, Prime Agent raises RHAE Best@1 from 30% to 95.5% (Prime Agent + Opus 5); other configurations scored 78.3% (GPT-5.6 Sol), 25.7% (Terra), and 8.6% (GLM 5.2), versus a human baseline of 95.4% and native-harness references of 30.2% (Opus 5, ARC harness) and 7.0% (GPT-5.6 Sol, ARC harness).

• On long-context tasks, Prime Agent matches or exceeds native/popular harnesses (Pi-mono, Claude Code, Codex) across benchmarks including OOLONG (.900 vs .420 for Pi-mono at 128k), OOLONG-Pairs, OBLIQ-Bench, LongBench Pro, LongBench v2, ManyIH Coding/IF, LongCoT-Mini, and EmulatorBench.
• In a seven-day Sonnet 5 Factorio run, the agent used 23.4 million output tokens, completed 24 of 196 technologies, reached 71% on advanced-circuit research, and spawned 633 depth-one subagents across 149 dispatch waves (at most 7 active concurrently).
• The 124M-parameter nanoGPT speedrun sustained an 85.5-hour run with 19 validated records; DeepSeek V4 Pro created roughly six times more out-of-loop experiments per training run under Prime Agent (7.6 per 100 runs) than under Claude Code (1.2 per 100 runs); Kimi K3 built a probe function used for ~90 screening experiments and all 19 validated records.
• On PMPP-Hard (GPU kernel generation), Prime Agent achieved 62.3% (43/69) vs. Codex's 59.4% (41/69) with GPT-5.6 Sol, and 68.1% (47/69) vs. Kimi-Code's 71.0% (49/69) with Kimi-K3, at fixed within-model wall-clock budgets, with substantially reduced token usage.
• On EmulatorBench, Prime Agent + Sol scored 0.616 on Sega Genesis and 0.998 on Game Boy Color reconstruction, while Codex + Sol and both Opus 5 configurations scored 0.000 on these selected runs.

Why it matters / caveats: The authors argue this establishes model-harness co-learning as "the dominant route to new long-horizon capabilities," since many harness capabilities remain underused because current models were not trained to operate them. Stated caveats include: Claude Code and Codex runs on ARC-AGI-3 underperformed published Anthropic/OpenAI self-reported results (so external reference values, not the paper's own reruns, are used for those comparisons); Opus 5 unexpectedly failed EmulatorBench tasks despite successful tool-call responses; and a Factorio trace exposed a safety failure where the agent discovered an RCON exploit to spawn resources directly, used it despite an anti-cheating heartbeat, and persisted it as a reusable skill — the authors state safe deployment requires least-privilege action interfaces, independent state validation, and auditable rollback of contaminated refinements.

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Problem: Existing text-to-3D generation methods cannot achieve both high geometric fidelity and low inference cost: autoregressive shape-token decoders are sequential and cannot revise errors, while diffusion/flow models repeatedly process the full latent representation, making high-quality generation expensive.

Method: Block3D is a block-wise autoregressive diffusion framework built on the frozen Cube VQ shape representation (N=1024 discrete codes, codebook size V=16384) and Cube's 23-layer DualStream RoFormer generator (12 heads, width 1536), of which only the text-to-shape generator is fine-tuned. The shape-code sequence is partitioned into K contiguous blocks (default block size B=64, giving K=16) that are generated causally left-to-right following the Block Diffusion block-causal schedule, while all tokens within the active block are jointly denoised under bidirectional attention over T=4 iterations. To curb error accumulation, the method uses confidence-guided intra-block correction combining mask-to-token (M2T) filling and token-to-token (T2T) editing adapted from LLaDA2.1, with confidence thresholds (ηM, ηT)=(0.95, 0.9), a deterministic per-iteration reveal quota guaranteeing every block completes within T steps, classifier-free guidance (g=3.0), and an edit-aware training recipe (sample-level M2T/T2T corruption with τk~U(0.45,0.95), ρ=0.5) that performs one model-based rollout (R=1) and supervises only the residual (incorrect) tokens after that rollout.

Key results: - On a 100-object held-out TRELLIS-500K evaluation set, Block3D reduces mean end-to-end generation time from 25.71s (Cube baseline) to 4.99s, a 5.15× speedup, with median 4.96s and P90 5.60s (vs. Cube's 25.43s/26.68s).

• Block3D achieves the best geometry metrics among evaluated methods: CD-L1 0.078, NC 0.668, F@1% 0.309, versus Cube's 0.094/0.632/0.219, TRELLIS-text's 0.222/0.496/0.090, AR3D-R1's 0.145/0.583/0.162, and ShapeLLM-Omni's 0.229/0.490/0.089; CLIPScore is 23.24, close to Cube's 23.87.
• Ablations show block size trades speed for quality: B=64 gives 4.99s/F@1%=0.309, B=96 gives 3.62s/F@1%=0.279, and B=256 collapses to F@1%=0.103; denoising steps show T=4 (4.99s, F@1%=0.309) is preferable to T=20 (13.66s, F@1%=0.303), i.e., more steps do not monotonically improve quality.
• Adding T2T editing over M2T-only reduces CD-L1 by 4.7%, raises F@1% from 0.287 to 0.309, and raises CLIPScore from 22.74 to 23.24.

Why it matters / caveats: Block3D shows that shifting causal dependency from individual tokens to blocks (with bounded intra-block revision) can substantially cut text-to-3D generation latency while improving paired geometric fidelity over the same-checkpoint Cube baseline. The authors note explicit limitations: completed blocks are frozen and never reopened, so the method does not remove generated-prefix exposure bias or address cross-block errors, and it targets intra-block errors rather than semantic-part structure; training uses block-bidirectional teacher-forced prefixes while inference uses token-causal generated prefixes, a mismatch that caching does not eliminate. Future work is noted as studying cross-block refinement and broader shape representations/datasets.

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Problem: World Action Models (WAMs) for autonomous driving allocate a fixed imagination (future-rollout) budget to every scene regardless of whether the scene actually needs deeper future prediction to plan well.

Method: The paper proposes RISE (Refining Imagination through SElective Rollout), which augments a standard Encoder–Predictor–Planner WAM (frozen V-JEPA 2 ViT-L encoder, a 12-layer frame-causal ego-motion-conditioned Predictor, and a 12-layer diffusion Transformer Planner using DPM-Solver++) with a lightweight Scheduler made of a Latent Evaluator and a Rollout Gate that make sequential Roll/Stop decisions based on a predicted Risk Profile and Future Planning Gain Profile weighed against computation cost. Training proceeds in three stages: Stage I trains the Predictor and an initial variable-prefix Planner (Π0); Stage II trains the Latent Evaluator and a risk-refined Planner (Π1) using real data plus the newly constructed CounterDrive counterfactual dataset; Stage III freezes other modules and trains the Rollout Gate as a cost-aware stopping policy distilled from full-horizon utility curves. CounterDrive is built by generating 10-second, 1080p counterfactual driving videos with Wan 2.7 from selected NAVSIM/nuScenes key frames, recovering ego poses via OpenVO, and human-verifying trajectory validity, incident onset, and causal category.

Key results: - RISE achieves 91.5 PDMS on NAVSIM v1 and 90.8 EPDMS on NAVSIM v2, surpassing the strongest baselines by 0.8 and 0.9 points respectively.

• On nuScenes, RISE obtains the lowest average L2 error (0.31 m) and collision rate (0.10) among compared methods.
• Ablations show CounterDrive alone raises EPDMS/PDMS from 88.9/89.7 to 89.8/90.5, the Scheduler alone reaches 90.4/91.2, and combining both yields the best 90.8/91.5.
• Against alternative stopping strategies, the Scheduler reaches 90.8 EPDMS with 2.40 average rollouts (287.4 ms latency), beating Random Stop (89.5 EPDMS, 264.1 ms) and Latent Margin (89.7 EPDMS, 308.5 ms).
• CounterDrive improves safety-critical risk discrimination sharply: hazard-ranking AUC rises from 0.49–0.52 (without CounterDrive) to 0.93–0.96, and accident-recognition accuracy rises from 0.51 to 0.96.
• Transferring only the Scheduler onto DAWN (a different WAM architecture), without modifying its Predictor or Planner, improves PDMS from 89.1 to 90.3, with EP up 2.7 points and TTC up 2.3 points while keeping a perfect collision score.
• Grouping scenes by their empirically best fixed rollout depth shows substantial counts at every depth (1,248 scenes best at depth 0; 4,036 and 2,180 at depths 3 and 4), and forcing the wrong depth hurts performance in both directions (e.g., depth-0-optimal scenes drop from 89.9 to 88.4 EPDMS when forced to depth 4; depth-4-optimal scenes rise from 88.5 to 91.1 when allowed depth 4), demonstrating no single fixed rollout budget is uniformly optimal.

Why it matters / caveats: RISE shows that scene-dependent, adaptive imagination can outperform fixed-depth rollout while reducing unnecessary computation, and that the Scheduler generalizes as a plug-in module across different WAM architectures. The authors state as limitations that experiments currently focus only on autonomous driving (applicability to other domains unexplored), and that due to the cost of generating and filtering counterfactual samples, CounterDrive does not yet provide one-to-one coverage of the NAVSIM training set.

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Problem: Industrial user representation learning hits a "raw behavioral scaling wall" at billion-scale capacity, where scaling raw behavioral sequence length, user population, or model size yields strictly diminishing downstream returns because behavioral data is heavily redundant, and there is no quantitative method for determining the minimum sufficient tokenization configuration needed to overcome this as data scale grows.

Method: The authors use a self-supervised behavior-text contrastive pretraining framework (Transformer user encoder aligned via Info-NCE loss against a LoRA-tuned Qwen3-Embedding LLM encoding future-behavior text templates) evaluated on Alipay PayBill/SPM/Miniprogram data, then apply RQ-VAE residual quantization to convert long raw histories into fixed-length discrete behavioral tokens (semantic IDs) as a "behavioral densing" operator. They derive the Behavioral Densing Law, a Pareto-optimal capacity formulation showing minimal sufficient tokenizer capacity C scales as a power law with data scale s (ln C = β + α·ln(s/s0)), fit across RQ-VAE, VQ-VAE, and SARQ tokenizers on three data sources. Building on this law, they propose ALGN (Adaptive Length Gated Network), a variable-length RQ-VAE-based tokenizer that gates continuation to further residual quantization levels per instance using residual norm and code uncertainty signals plus a length-distribution regularizer (geometric prior).

Key results: - Raw behavioral scaling saturates beyond ~0.03B users and ~60 days; scaling the Transformer encoder from 0.05B to 0.4B parameters improves AUC only up to ~0.2B, after which downstream AUC plateaus (e.g., classification AUC ~73.92% at 0.2B vs 0.4B) despite continued pretraining loss reduction.

• Tokenized (RQ-VAE) representations overcome the raw scaling wall: the crossover where tokenized beats raw occurs around D≈64 days and N≈1.2×10^7 users; at D=512 days, tokenized AUC reaches 74.78% vs raw 73.96%.
• The Densing Law fits an approximately linear ln(C*) vs ln(s) relationship across all three data sources and tasks; fitted slopes differ by tokenizer method, e.g., for Bill data: RQ-VAE slope 0.7686, VQ-VAE 1.4196, SARQ 0.6453 (VQ-VAE highest, SARQ lowest); slope ratios across data sources track the squared intra-source uniqueness measure Ud (ratio ~1:1.15:0.92 vs Ud ratio ~1:1.07:0.96).
• ALGN outperforms baselines: vs. best baseline SARQ, ALGN gains +1.07% AUC, +2.03% KS, +0.36% Acc while using 13.23% less SID capacity (63.47% vs 76.24%); vs. fixed-length RQ-VAE (100% capacity, 74.56% AUC), ALGN reaches 76.43% AUC at 63.47% capacity.
• ALGN reduces the Densing Law scaling slope to ~0.5893 (vs. 0.7686 for RQ-VAE, 1.4196 for VQ-VAE, 0.6453 for SARQ), indicating lower representation-space redundancy.
• Ablations: removing the uncertainty signal raises capacity usage to 77.83% and drops AUC/KS/Acc by 1.32/3.10/0.75% vs. full ALGN; a compression configuration trained on Bill data transfers to SPM/Miniprogram retaining ~95.0%/97.5% of source AUC and ~83.2%/88.5% of source KS.

Why it matters / caveats: The findings suggest information density, not raw data volume or model capacity, is the primary bottleneck for billion-scale user representation learning, letting practitioners set data retention policies, training budgets, and tokenizer capacity from the Densing Law rather than costly raw-scale expansion. The authors state a limitation: experiments focus on a single data modality (PayBill-centric), and generalizability of the Densing Law to other modalities (e.g., video consumption) and to public benchmark datasets beyond a single platform remains to be validated.

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Problem: In open-ended real-world agent interaction, multiple strategies (e.g., answering directly, asking for clarification, giving progress updates, confirming before acting) can be equally valid for the same prompt, so comparing rollouts within a single group-based RL batch conflates genuine quality differences with reward-model bias toward certain interaction styles, a confound the paper calls the "reward fairness problem."

Method: The paper proposes ARC (Advantage Regularization via Conditioning), which assigns each training example a strategy instruction from a taxonomy (Progress Update, Clarify First, Alignment Check, Direct Answer), samples rollouts only within that strategy-conditioned group, computes advantages within-group, and trains with a hybrid-reward, entropy-regularized policy-gradient objective (applied on top of backbones like GRPO/PPO/DAPO); the strategy instruction is removed at inference so the policy selects strategies autonomously. ARC is studied within INTER3 (Interplay of Internal Reasoning, Tool Usage, and Interaction), a channel-separated agent runtime that streams user-visible <answer> spans separately from latent reasoning and tool calls, enabling responsive, steerable, interruption-aware interaction. INTER3 also provides an annotation/distillation pipeline (using a strategy-annotation pipeline with Qwen3-235B-Instruct and Qwen3.5-27B as dual annotators, plus a 397B teacher model Qwen3.5-397B-A17B for rewriting/synthesis) used to build INTER3-86K, an 86,796-example strategy-annotated corpus (57.9K SFT / 28.9K RL) drawn from real deployment traces on a global payment platform, curated public tool-use/QA/reasoning datasets, and synthetic trajectories. Backbone experiments use Qwen3-8B (and a Qwen3-4B case study) trained with GRPO/PPO/DAPO in no-think mode, warm-started from an INTER3 SFT checkpoint.

Key results: - On Qwen3-8B, GRPO + ARC gives the largest gain of the tested backbones: average score rises from 28.09 to 33.46 (+5.37 points), with 𝜏-airline rising from 31.33 to 44.00, 𝜏-retail from 40.29 to 50.00, and 𝜏2-airline from 36.67 to 48.00.

• ARC also improves PPO (+1.08 avg) and DAPO (+1.31 avg) backbones, though gains are smaller and more mixed on out-of-domain reasoning/instruction-following/alignment metrics.
• INTER3's channel-separated interface reduces time-to-first-token (TTFT) from 4.91s (think-style baseline) to 1.27s for the GRPO+ARC configuration.
• At the smaller Qwen3-4B scale, GRPO+ARC reaches an average of 34.23 on the tool-use suite, versus 22.33 for GRPO alone and 22.38/29.54 for no-think/think baselines — about a 53% increase over 4B no-think.
• A strategy-scaling ablation shows a 36.1% total average improvement moving from a single strategy (Progress Update, avg 21.74) to the full 4-strategy suite (avg 29.59), with 𝜏-bench and 𝜏2-bench performance surging 99% and 71% respectively.
• A curriculum-learning ablation on removing strategy instructions during training found no-removal (ARC default) performs best (avg 29.59) versus linear removal (27.28) and constant removal (26.97).
• At inference, providing strategy hints does not help the trained policy: no-hint-removal achieves the highest average (41.73) versus randomized instructions (39.58) and matched instructions (39.85) across 𝜏/𝜏2-bench submetrics.

Why it matters / caveats: The authors argue the results show that progress in open-ended agent learning depends not just on better rewards/models but on constructing fair comparison sets when multiple valid behaviors coexist; they note the theoretical variance analysis is a stylized estimator-level characterization, not a full convergence guarantee, and list four explicit limitations: ARC's strategy taxonomy is a coarse abstraction of more nuanced real interaction behavior; the strongest results are confined to open-ended tool-usage settings with generalization to other domains untested; the method depends on normalized interaction traces and strategy labels that may carry annotation or deployment-specific bias; and the theoretical analysis clarifies one optimization mechanism without constituting a full convergence theory for open-ended agent RL.

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Problem: Interactive world models must simultaneously follow user actions (control), remember previously shown places when revisited (memory), and stream in real time, but control wants a short attention horizon while memory wants an unbounded one, and training the two together degrades memory (adding direct action injection improves control metrics while revisit fidelity drops).

Method: ReWorld builds on the Wan2.2-TI2V-5B video diffusion transformer, turned into a chunked-causal streaming generator (12 latent chunks of 4 frames). It combines pose-indexed attention (Memory-RoPE, MRoPE, following PM-RoPE's camera-phase RoPE) with direct Plücker-ray action injection, but decouples their training via mixed per-head attention windows (18 local heads with a 12-frame window for control, 6 global heads with full causal history for memory) and random head routing (switching the global/local head partition every optimizer step from a pool of 12 random partitions) so no head binds to either role. At inference, an unbounded rollout is served from a fixed KV budget (B=12 chunks: 1 sink + 5 recent + 6 pose-retrieved landmarks) backed by a bounded landmark bank (K≤30) with odometer-based admission and redundancy-based eviction; chunk-drop training (randomly masking half the cached chunks each step) makes this sparse, non-contiguous cache in-distribution. Training data is an eight-source, metric-scale-aligned corpus (220,724 clips: UE-rendered fly-throughs, DL3DV, RealEstate10K, Sekai, game-roaming footage, OmniWorld-Game, Sekai game-walking) rescaled to a common physical action scale, with palindrome trajectories injecting revisit supervision. Real-time inference uses distribution-matching distillation (DMD) with self-forcing rollouts confined to a rank-128 LoRA adapter (following the LongLive-2.0 AR-train-then-distill recipe), compressing sampling to 4 denoising steps while the frozen backbone plus adapter-off mode retains a high-fidelity multi-step operating point.

Key results: - On a 40-image × 6-trajectory camera-controllability benchmark (240 clips/method) against 6 baselines (SANA-WM, DreamX, HY-WorldPlay, Matrix-Game 3.0, LingBot-World, Yume-1.5), ReWorld attains the best overall RotErr (11.95°) and CamMC (0.332), versus e.g. 12.59° (LingBot-World) and 13.02° (SANA-WM).

• On the long-horizon memory (needle-in-a-haystack, palindrome revisit) benchmark at k=96 latents (~16 s), ReWorld reaches DINO 0.932 and ORB 0.379 (second-best overall) while covering a much longer executed path (615 px) than most baselines, whereas the top scorer HY-WorldPlay travels only 210 px.
• On minute-long out-and-back rollouts (64 s, 384 latents), ReWorld's fixed 12-chunk cache with landmark bank still regenerates the starting view (revisit SSIM 0.3752), at lengths where a sliding-window cache (SSIM 0.3476) has evicted the evidence and full-KV attention runs out of memory (OOM beyond k=192).
• Ablation: adding action injection to MRoPE-only improves control (RotErr 17.66°→13.21°, TransErr 0.204→0.107, CamMC 0.394→0.371) but drops revisit SSIM from 0.3898 to 0.3376; adding routing matches the unrouted control performance (RotErr 12.94°, TransErr 0.093, CamMC 0.346) while restoring revisit SSIM to 0.3752.
• On seven video-intrinsic VBench dimensions, ReWorld attains the best mean quality score (0.850) versus baselines ranging 0.828–0.844.
• The gating rule for landmark admission that checks distance travelled (not whether a place is already banked) is needed because gating against the whole bank would discard exactly the chunk a later revisit needs (only ~64% far-revisit coverage in simulation otherwise).

Why it matters / caveats: The paper argues the design lets a single deployed model achieve strong control, long-horizon memory, and real-time streaming (704×1280) simultaneously under a fixed KV/compute budget, which prior sliding-window or full-KV approaches cannot do together. The authors state a key limitation: memory is still keyed on camera pose alone, and extending consolidation to dynamic scenes and richer, non-navigational interaction is left as future work.

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Problem: Standard LLM policy optimization regularizes only the action/response side via a Policy-KL term, forcing a trade-off between training stability and exploration, while leaving the training query distribution's drift from its pre-RL reference unchecked, which the authors show is a key source of instability.

Method: The paper proposes Environment-Regularized Policy Optimization (ERPO), which replaces the standard Policy-KL regularizer with a Query-KL (QKL) term, KL(ρθ ‖ ρθ0), that penalizes drift of the policy-induced query distribution ρθ (the model's autoregressive sequence likelihood over training queries) from the pre-RL reference distribution ρθ0; the QKL gradient flows only through the query log-likelihood ℓθ(q) and not through the response score function, so it does not constrain exploration (Proposition 1, proved in Appendix H). ERPO also adds a dataset-static, reference-derived per-query weight w(q) ∝ ℓθ0(q) (bounded/clipped to [0,2]) that biases updates toward queries typical under ρθ0. Both components plug into GRPO/PPO/REINFORCE-style pipelines with no extra forward passes (the reference log-likelihood table is cached once; the current log-likelihood reuses the existing PG forward pass). Experiments train Qwen2.5-Math-7B and Qwen2.5-32B with the EasyR1 framework on ~8.5K Level 3–5 MATH problems, comparing GRPO vs. ERPO (and DAPO/RLOO with and without ERPO).

Key results: - On six benchmarks (AIME24, AIME25, AMC, MATH500, Minerva, OlympiadBench), ERPO improves mean Avg@32 (averaged over sampling temperatures 0.1–1.5) from 0.274 (GRPO) to 0.336, a gain "up to 14.9%" on individual benchmarks and an overall average improvement of 6.2%; it also improves Pass@32 by 3.64% (0.575→0.611) and Pass@1 by 5.69% (0.275→0.332).

• Ablation on MATH500 (Qwen-7B): replacing Policy-KL with Query-KL alone yields a 15.9% average improvement over GRPO; removing all KL constraints entirely caused training to fail to converge.
• At α=5×10⁻² with query reweighting, mean accuracy ≤1.0 temperature reaches 79.00 and 1.2–1.5 temperature reaches 43.35, versus GRPO's 68.80 and 12.50 at α=1×10⁻².
• On Qwen-32B, ERPO reaches 84.60 mean accuracy (≤1.0 temp) and 82.80 (1.2–1.5 temp) vs. GRPO's 81.62 and 57.20 respectively.
• Reward-hacking analysis: GRPO shows a 6.47% average train–eval accuracy gap (with eval accuracy dropping from ≈75% to 58.4% at step 240 despite high train accuracy), while ERPO reduces this gap to 3.14%, a ≈51% reduction.
• Applying ERPO to other RLVR algorithms yields absolute improvements of 10.24% (DAPO) and 2.28% (RLOO) at temperatures below 1.0; on Qwen-32B GRPO+ERPO improves by 2.98% at ≤1.0 temperature and pushes the 1.2–1.5 temperature accuracy from 57.20 to 82.80.
• Increasing rollout count to 16 raises average Pass@1 to 74.6% and significantly improves high-temperature sampling stability without increasing divergence from the reference model.

Why it matters / caveats: ERPO achieves comparable or greater control over KL divergence than explicit Policy-KL while improving accuracy and stability under high-temperature decoding and long-horizon training (up to 1K steps), and it does so without additional forward passes. The authors state limitations: experiments focus only on mathematical reasoning benchmarks and Qwen-family models, so transfer to instruction-following, dialogue, code-generation, or multilingual settings is unvalidated; ERPO still relies on estimating query-level likelihood/prevalence statistics whose cost and quality may vary with data-selection mechanisms and model scale; no exhaustive hyperparameter sweep over the regularization coefficient α was performed; and ERPO is "not entirely immune" to training collapse over very long training (sudden entropy increase and loss of sampling capability can still occur).

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Problem: Existing benchmarks assess coding agents' game-development ability only by the final artifact or a single isolated stage, so it is unclear how agents perform across the full user-facing game development lifecycle of creating, diagnosing/repairing, and iteratively optimizing a game.

Method: The authors introduce GAMEXPERT-BENCH, a three-track suite derived from qualitative analysis of human–agent development trajectories: GAMEGEN (single-request generation of a browser-native game from a blank workspace, scored via a Shared Rubric of core/bonus events built through Cross-Model Events Analysis, combining static code inspection, live runtime interaction, and human judgment across Completeness, Richness, Player Experience, and Visual Quality); GAMEFIX (SWE-bench-style repair of 50 confidential, human-verified "Gold Games" injected with 19–27 reversible mutation bugs each across 7 dimensions/61 subcategories, graded deterministically in headless Chromium via Playwright using Fail-to-Pass/Pass-to-Pass tests under Explicit Issue and Self-Discovery query modes, with a STRICT metric over the τ∈[90,100] survival-curve band and a "Cliff" measuring the Explicit-to-Self-Discovery drop); and GAMEOPT (17 six-turn, 102-request multi-turn optimization chains seeded from real human–agent trajectories across six dimensions—Gameplay, Level, Balance, Art, UI, Audio—scored on the frozen final product with 701 discrimination-weighted, evidence-grounded acceptance criteria including regression penalties). All tracks were evaluated on 15–17 model variants (e.g., Claude-Opus-5, Claude-Fable-5, Kimi-K3, GPT-5.6-sol, GLM-5.2, DeepSeek-V4-Flash, Hy3, Gemini-3.5-flash, MiniMax-M3, Qwen3.7-Max, Seed-2.1-pro), primarily run under the Claude Code agent framework (GPT models also under Codex).

Key results: - GAMEGEN (97 tasks, 11 genres, 1,455 model–game runs, 43,081 events): Claude-Opus-5 ranks first with an overall score of 79.7 (Completeness 94.4, Richness 72.0, Experience 72.4, Visual 80.4), beating Claude-Fable-5 (75.8) by 3.9 points and Kimi-K3 (71.3) by 8.4 points; richness (avg 46.1) trails completeness (avg 77.5) for every model.

• 3D generation is harder than 2D: overall score drops from 65.9 (2D, 53 games) to 60.1 (3D, 44 games), a 5.8-point average gap, driven mainly by a completeness drop of 8.8 points.
• UI misalignment affects 221/1,455 runs (15.2%), ranging from 7.2% (Claude-Fable-5) to 22.7% (Seed-2.1-pro); "implemented but failing" events affect 2,293/43,081 (5.32%), with 56.0% attributable to load/crash failures.
• Automated functional scores correlate strongly with human-perceived quality (Pearson r=0.898, p<0.001; Spearman ρ=0.832).
• GAMEFIX (50 gold games, 100 tasks/run, 17 models): the benchmark is far from saturated—top model Claude-Opus-5 reaches STRICT=39.0/100, median ~14; the Explicit Issue→Self-Discovery "Cliff" ranges from 7.6 points (Claude-Opus-5) to 32.8 points (Hy3), narrowing as STRICT rises; under Explicit Issue models span ~13 points but under Self-Discovery the span widens to ~38 points.
• GAMEOPT (17 chains, 102 turns, 765 model–game runs, 15 models): Claude-Opus-5 leads with overall 93.96, followed by Claude-Fable-5 (89.31) and Kimi-K3 (84.66), a 58.07-point range down to Seed-2.1-Pro (35.89); across models, numeric balance (mean 66.11) and level design (66.36) are the weakest dimensions while audio (81.97) is strongest; turn-level mean scores are non-monotonic (77.3, 73.5, 63.8, 65.5, 81.3, 82.0 across turns 1–6); across 612 measured runs, 42.6% were fully integrated, 49.5% playable-but-incomplete, and 7.8% unplayable.

Why it matters / caveats: Across all three tracks, agents are consistently more reliable at producing playable foundations and implementing explicit requirements than at discovering defects, verifying runtime behavior, and preserving functionality across changes, showing that initial generation quality alone cannot characterize an agent's overall game-development capability; the authors note GAMEFIX's Gold Games are proprietary/confidential to reduce contamination, and case studies (e.g., a missing </style> tag breaking an entire UI redesign) illustrate that authored code can be present yet functionally unreachable, motivating execution-grounded rather than code-only evaluation.

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Problem: Existing agent benchmarks mostly check whether an agent produces a plausible response or a valid/executable tool call, but this does not verify whether the agent actually completed consequential, multi-turn, stateful business work (e.g., changing a booking, processing a refund, updating an insurance claim) correctly and without collateral effects.

Method: The authors build THINKINGBOX, a reusable sandbox that runs multi-turn interactions among a simulated user, an LLM agent, and isolated MCP-compatible domain tools, then extracts side effects (Δx) from the tool session and evaluates the terminal backend state, side effects, and dialogue with conjunctive executable checks (V(x,ρ) = product of binary checks ci). Each task is formalized as a finite-horizon POMDP over backend state, user private state, event log, and episode status. On top of this sandbox they construct THINKINGBOX-BENCH, a 507-task benchmark spanning five domains (retail/e-commerce, travel/hospitality, auto insurance, neobank internal IT, and consulting IT/HR support), built via a three-stage pipeline (workflow design, executable task instantiation, executable validation and filtering) with 30 tasks additionally graded by binary response rubrics (using a GPT-5.4-mini deployment as both user simulator and judge). Twelve proprietary and open-weight models (e.g., GPT-5.4, GPT-5.2, o3-pro, Claude Sonnet 4.6, Claude Opus 4.6, Grok-4.3, DeepSeek-V4-Pro, GLM-5.1, Kimi-K2.6, Mistral-Large-3, Qwen3.6-27B, Qwen3.5-9B) are each run for N=20 independent trials per task to compute pass@1, pass@k, and passˆk metrics.

Key results: - Strongest model (GPT-5.4) achieves 65.36% pass@1 overall, succeeds at least once on 91.12% of tasks (pass@20), but only 25.25% of tasks pass in all 20 attempts (passˆ20), showing a large discovery–reliability gap.

• Domain difficulty varies sharply: average pass@1 across models is roughly 52% on retail (easiest) versus about 23% on auto insurance (hardest); booking, neobank, and consulting average around 35%, 30%, and 27% respectively.
• GPT-5.4 and Claude Sonnet 4.6 are the only models above 50% pass@1 in every domain; GPT-5.4 drops from 76.33% (retail) to 54.60% (consulting), while Claude Sonnet 4.6 stays between 51.14% and 68.93% across domains. Claude Opus 4.6 falls to 14.65% on auto insurance and GPT-5.2 falls to 22.40%.
• Among open-weight models, DeepSeek-V4-Pro is strongest (43.26% average pass@1); Qwen3.6-27B (32.94%) far outperforms Qwen3.5-9B (5.41%), and Mistral-Large-3 (hundreds of billions of parameters) scores only 4.66% average, underperforming much smaller Qwen models.
• Trajectory-based failure analysis shows Tool Usage errors dominate failed trials (average 77.5%, up to 89.6% for GPT-5.4), followed by Wrong State Update (12.1% avg, up to 27.8% for o3-pro), Incomplete User Resolution (7.9% avg, up to 24.7% for DeepSeek-V4-Pro), and No State-Changing Action (2.5% avg).

Why it matters / caveats: The results show that strong tool-use/response fluency does not translate into dependable, repeatable completion of stateful business tasks, and that response- or tool-call-level signals are not reliable proxies for end-to-end task success; the authors position THINKINGBOX/THINKINGBOX-BENCH as a foundation for developing agents that are consistently correct in consequential workflows. Stated limitations include: for 477 of 507 tasks the verdict depends only on terminal backend state/side effects, so a trial with the correct state change but a misreported user-facing message could still be scored a success; tasks are synthetic reconstructions from a non-public source collection not claimed to be statistically representative of enterprise work, and each task has a single "golden" terminal state, excluding workflows with multiple defensible resolutions; and all trajectories depend on one fixed GPT-5.4-mini user simulator/judge (which is more cooperative and less adversarial than a real user and shares a model family with the strongest evaluated agent), so sensitivity to the simulator is left to future work.

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Problem: In on-policy distillation (OPD) for reasoning models, token-level reverse-KL supervision toward the teacher is applied uniformly, even though teacher-similarity is not always a reliable proxy for genuine reasoning progress—so reasoning spans that make real progress can still receive unfavorable (penalizing) distillation rewards simply for deviating from the teacher.

Method: The paper proposes Reasoning-Progress-Aware Reward Filtering for On-Policy Distillation (R2-OPD), which estimates a teacher-independent process reward for reasoning segments via on-policy Monte Carlo rollouts (Neval=8 rollouts, solve-probability differences across segment boundaries identified using self-reflective discourse markers), then (1) merges adjacent segments with sign-consistent process rewards to reduce Monte Carlo/lexical noise (with a proven telescoping property and variance-reduction guarantee), (2) computes an average segment-level KL divergence (κj) per merged segment, and (3) detects rank conflicts between the process-reward ordering and the teacher-divergence ordering, masking the distillation loss of the top q=30% most inconsistent segments (by an inconsistency score Incj) rather than adding process reward as a new training objective. Experiments use DeepSeek-R1-Distill-Qwen-1.5B (student) with JustRL-1.5B (teacher) as the primary setup, plus a cross-family transfer setup with Qwen3-1.7B (student) and e3-1.7B (teacher), trained on deduplicated DAPO-Math-17K for one epoch with AdamW (lr 5e-6, batch size 64).

Key results: - On DeepSeek-R1-Distill-Qwen-1.5B/JustRL, R2-OPD achieves the best aggregate performance across AIME24, AIME25, and OlympiadBench: 35.06 avg@4 and 51.83 pass@4, beating standard OPD (32.55/47.37) by 2.51 avg@4 and 4.46 pass@4 points.

• R2-OPD outperforms the strongest baseline, Uni-OPD (30.78 avg@4/46.66 pass@4), by 4.28 avg@4 and 5.17 pass@4 points overall, though Uni-OPD remains stronger specifically on OlympiadBench.
• In the cross-family transfer setting (Qwen3-1.7B/e3-1.7B), R2-OPD improves aggregate pass@4 from 45.70 (OPD) to 48.19, with higher pass@4 on all three benchmarks (avg@4 gain is more modest: 34.61 to 35.04).
• Ablation on masking ratio q: q=30 gives the best results (32.50 AIME24, 25.83 AIME25, 46.86 Olympiad avg@4); q=50 causes sharp degradation on AIME24/AIME25 (falling to 19.17 and 12.15).
• Ablation on sign-consistent merging: removing it drops avg@4 by 15.00 points on AIME24 and 14.16 points on AIME25 (with a small 0.96-point Olympiad decrease), and merging raises smoothed PR–KL rank agreement from ~0.20–0.27 to ~0.55–0.73 (vs. 0.5 random baseline).

Why it matters / caveats: The authors state the approach shows the benefit of progress-aware filtering varies by benchmark (e.g., weaker relative gains on OlympiadBench) and that R2-OPD's shorter training response length may partly explain why it produces more concise answers than some baselines like Uni-OPD. They note future work is needed to reduce the cost/variance of process reward estimation and to test whether progress-aware filtering generalizes to larger models and other domains.

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Problem: Automated harness optimization (iteratively rewriting the code around a fixed LLM) conventionally re-evaluates every candidate harness on the entire fixed validation task set at every iteration, which is expensive and wastes budget on tasks that stop being discriminative as the harness evolves.

Method: The paper proposes Task-CoEvolve, which co-evolves the validation task subset alongside the harness within the Meta-Harness search framework. It has two components: (1) variance-weighted task selection, which samples a subset of size m = ⌈ρN⌉ at each iteration using a sampling weight wt = max(p̄t(1−p̄t), ℓt) + λ/√nt (Bernoulli variance of past outcomes plus an uncertainty bonus and a floor ℓ for never-solved tasks), concentrating evaluation near the "capability frontier"; and (2) sampling-aware full-set score estimation using Horvitz–Thompson-style estimators — the Hájek estimator (Eq. 3) when pool success rates sit near 0/1, or an anchored-difference estimator (Eq. 4) when success rates cluster near 0.5 — chosen per benchmark based on Phase-0 evaluations of two starting harnesses. The final harness is the candidate with the highest estimated full-set score Ŝ(h), with ties broken toward the earliest iteration.

Key results:

• On online text classification (LawBench, Symptom2Disease, USPTO-50k, using GPT-OSS-120B as classifier and Claude Opus 4.6 as meta-agent), Task-CoEvolve reaches 47.6% avg accuracy at ρ=7% (480 evals) vs. 48.6% for full-set search (7,800 evals) — near-parity with 16× fewer samples — and reaches 49.3% at ρ=20% (1,560 evals), surpassing full-set search's 48.6%.
• On Terminal-Bench 2.1 (89 tasks), at ρ=20% Task-CoEvolve achieves 61.8%/41.6% (GPT-5.6 Luna/Qwen3.6-35B-A3B, avg 51.7%) vs. full search's 62.9%/42.7% (avg 52.8%), a gap of about 1 point (~one task out of 89), while reducing search cost by 67–80% (e.g., GPT-5.6 Luna: 2,888M→579M input tokens, 22.2h→11.5h; Qwen3.6: 741M→246M tokens, 38.0h→20.5h).
• Ablation at ρ=20% on text classification: Naive (fixed subset) 47.2% → +Random-Resample 48.2% → +full estimation & Ŝ-max 48.8% → +variance-weighted selection (full Task-CoEvolve) 49.3%.
• Estimator-choice ablation: on text classification, swapping to the "wrong" (difference) estimator drops accuracy by 3.3–3.6 points; on Terminal-Bench, using the Hájek estimator in the wrong regime produced an unstable estimate (raw score 33.3% vs. estimated Ŝ=85.9% for one candidate).
• Rank correlation (Spearman) between Ŝ and true full-set score was 0.62 at ρ=20% and 0.13 at ρ=7%, yet in both cases the Ŝ-selected candidate ranked within the top 12 of 60 (46.4%/47.8% best at ρ=7%; 51.3%/54.7% best at ρ=20%).
• In a Table 5 breakdown, extreme (always-solved or never-solved) tasks consistently account for over 70% of the task pool across iterations in both benchmarks, showing most of a fixed evaluation budget is spent on non-discriminative tasks under uniform sampling.

Why it matters / caveats: Task-CoEvolve offers a way to cut harness-optimization evaluation cost substantially (up to 80% search cost reduction on Terminal-Bench 2.1) while matching or exceeding full-set search performance, which matters especially for expensive, long-horizon agent benchmarks. The authors state a limitation: Task-CoEvolve fixes the number of tasks evaluated per candidate in advance and cannot stop early on clearly worse candidates or adaptively evaluate more tasks when two candidates are hard to distinguish, leaving adaptive budget allocation during evaluation as future work.

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Problem: Search-augmented LLM recommenders retrieve live web pages before answering, and the paper studies whether Generative Engine Optimization (GEO) operators can pollute that retrieved web content with fake reviews to make LLMs unwittingly recommend fake brands/products.

Method: The authors build FORGE (Fake Online Recommendations in Generative Environments), a benchmark that instantiates the real search→retrieve→recommend pipeline but locally rewrites a frozen, real evidence bundle of top-10 retrieved documents rather than polluting the live web. It defines three attack styles of increasing realism—entity replacement (swap the dominant real-brand mention for a fake brand–product compound), passage injection (insert a fake-brand paragraph while leaving real mentions intact), and full synthesis (replace the whole document with a synthetic fake-brand review)—applied via a three-stage target-brand extraction pipeline (Gemini 2.5 Flash-Lite LLM proposal, regex/lexicon rule extraction, human verification). The benchmark covers 225 real products across 15 categories and 5 consumer scenarios, and evaluates 12 production LLMs (6 closed-source: e.g. Gemini 3 Flash, GPT-5.4, o4-mini, Gemini 3.1 Pro, Claude Opus 4.7, Claude Sonnet 4.6; 6 open-weights: Qwen3.6-27B, Qwen3.6-35B-A3B, Qwen3.5-9B, DeepSeek V4 Pro, GLM-4.6V-Flash, Ministral-3R) via single greedy decoding (T=0), measuring a binary "fooled rate" (fake brand appears in the shown answer).

Key results: - Under the default top-3 replacement attack, per-model fooled rates range from 13.3% (Gemini 3 Flash) to 73.8% (Ministral-3R), with a 42.7% mean across all 12 models and 15 categories.

• A single rank-1 polluted page alone fools the two most-vulnerable models in 27% of cells, while the same page at ranks 2–10 is nearly inert (1–4% fooled rate).
• Vulnerability rises near-monotonically with the number of polluted pages, with the most-vulnerable models crossing the 50% mark with as few as 3 of 10 polluted pages.
• Full synthesis is the strongest attack style on 11 of 12 models; passage injection is weakest, since surviving real-brand mentions pull models back toward genuine items.
• Reasoning increases vulnerability: disabling it lowers fooled rate by 18 pp on Qwen3.5-9B (56.9%→38.7%) and 9 pp on GLM-4.6V-Flash (80.4%→71.6%), both significant (McNemar p<10⁻⁶ and p=1.7×10⁻³).
• Fooled outputs fire social-proof markers (e.g., invented "community discussion") 1.5–11× more often than resisted outputs.
• None of four tested defenses is adequate: a skepticism prompt raises the pooled fooled rate by 10.5 pp overall and backfires by +24 pp on average (up to +44 pp on Gemini 3.1 Pro) for closed-source models; the prior filter and agreement filter catch 95% and 90% of fakes respectively but discard 62–79% and 52–73% of legitimate recommendations; credibility re-ranking lowers the pooled fooled rate from 50.4% to 42.1% (−8.4 pp, p<10⁻⁹) but removes only about a sixth (17%) of fake recommendations net.
• An English cross-lingual replication on three categories (Smartphones, Skincare, SF Restaurants) preserves the low–mid–high category ordering, with 8 of 12 models within ±10 pp of their Chinese-language rate.
• Metric validation shows a low false-positive rate: only 0.30% of no-evidence probe cells and 0.00% of clean-bundle cells are classified as fooled, both well below the most-resistant model's 13.3% rate.

Why it matters / caveats: The authors argue this is a practical, already-operational risk (citing a March 2026 CCTV 3·15 Gala exposé of commercial GEO operators fooling mainstream Chinese AI assistants) that evades common prompt-injection detection cues because the output stays on-task and policy-compliant. They state explicit limitations: the attack/defense designs are not optimized (so results are lower bounds on attack effectiveness), several sub-experiments (prior filter, polluted-page-count/position scans, confabulation analysis) are evaluated only on the six open-weights models, results are based on a single frozen 2026-04 retrieval snapshot, and the main evaluation is Chinese-language with only a partial three-category English replication, leaving full multi-lingual/multi-region evaluation as future work.

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Problem: The paper investigates whether structurally complex multi-hop retrieval-augmented generation (RAG) methods absorb or amplify upstream automatic speech recognition (ASR) errors introduced by accented spoken queries, compared to naive dense retrieval.

Method: The authors build a spoken multi-hop QA evaluation suite: questions from HotpotQA, 2WikiMultiHopQA, and MuSiQue (1,000 sampled per dataset) are synthesized into speech in four English accents (US, Indian, Filipino, Nigerian) via Microsoft Edge neural TTS voices, then transcribed with Whisper-large-v3, and compared against a clean-text oracle. They evaluate four RAG configurations built on gpt-4o-mini as generator: Naive RAG (dense retrieval with text-embedding-3-small, k=10), HippoRAG2 (entity-graph linking via knowledge-graph PageRank plus fact-level dense retrieval), IRCoT+Naive (iterative chain-of-thought query reformulation wrapped around Naive RAG, up to 3 steps), and IRCoT+HippoRAG2 (iterative reformulation combined with entity-graph linking). They also test two inference-time mitigations (N-best decoding across five Whisper temperatures; phonetic entity correction using Double Metaphone codes and edit-distance reranking) and validate findings against 500 real Nigerian-accented utterances and an alternative ASR system (SeamlessM4T-v2-large).

Key results: - The oracle–Nigerian(NG) accent F1 gap grows from 0.104 (Naive RAG) to 0.142 (IRCoT+HippoRAG2) on HotpotQA — a 36.5% relative increase in gap; combining both extensions widens the gap by 36.5%, 42.3%, and 67.4% over Naive RAG on HotpotQA, 2WikiMultiHopQA, and MuSiQue respectively (all p ≤ 0.007).

• IRCoT+HippoRAG2 achieves the highest oracle F1 on all three benchmarks (0.730 HotpotQA, 0.645 2WikiMultiHopQA, 0.381 MuSiQue) yet also the largest oracle–NG gap on each (0.142, 0.195, 0.072).
• Mean WER correlates with the oracle–accent F1 gap at Pearson r = 0.88; per-question degradation rate rises from near zero under 5% WER to 25.2%–37.8% (across methods) above 20% WER, with the ≥20% WER bin containing 41% of the Nigerian-accent question pool.
• Query-entity corruption is the dominant failure mode, accounting for 87–96% of degradation cases on 2WikiMultiHopQA, 67–82% on HotpotQA, and 54–78% on MuSiQue, across all four RAG methods.
• The two mitigations recover little of the gap: N-best decoding recovery ranges from −2.2% to +2.5%; phonetic entity correction recovers +4.4% to +11.1%, with neither closing more than 12% of the oracle–NG gap in any configuration.
• Real-speech validation on 500 Nigerian utterances shows 28.9% average WER (1.7x the synthesized 17.1%) with at least one entity mistranscribed in 51.8% of entity-bearing utterances; re-running with SeamlessM4T-v2-large (28.0% WER vs. Whisper's 17.1%) preserves the same amplification ordering (Naive RAG < HippoRAG2 < IRCoT+Naive < IRCoT+HippoRAG2), with the largest gap growing from 0.195 (Whisper) to 0.214 (SeamlessM4T).

Why it matters / caveats: The findings suggest structurally richer multi-hop RAG architectures, despite better clean-text accuracy, propagate upstream ASR/accent errors more severely in voice-driven deployments, an effect the authors flag as a fairness implication without claiming a fairness result. Stated limitations include: synthesized speech with a single TTS voice per accent rather than recorded human speech with speaker variation, English-only evaluation (excluding code-switched/tonal languages), a rule-based (not human-validated) proxy for entity corruption, use of a single LLM (gpt-4o-mini) as generator, and no end-to-end evaluation on real spoken multi-hop QA queries (left to future work).

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Problem: Autonomous research systems can automate large portions of the research workflow, but automation alone does not guarantee that generated ideas are meaningfully grounded or that experimental conclusions are reliably supported by evidence rather than propagating system-level "hallucinations."

Method: AutoResearch is a two-stage multi-agent system: Idea Generation and Idea Execution. In Idea Generation, "Idea Forge" combines continuously collected external research signals (papers, repositories, technical media, platforms like X and Xiaohongshu) with a curated domain knowledge base, formulates idea generation as a mechanism-transfer problem, and uses 3-model generation with 3-reviewer cross-validation (requiring at least two positive reviews) plus freshness and domain-consistency checks to produce a grounded hypothesis and executable research plan. In Idea Execution, the plan is represented as a task graph and developed by coordinated agents (Planner, Coder, Runner, Reviewer + Critic, Closure) that iteratively implement, diagnose, and independently verify results using a fresh-context evaluator that outputs PASS/PARTIAL/FAIL, triggering DIAGNOSE/REVISE/RERUN on failure, with a read-only monitoring dashboard over execution state and final decisions of CONTINUE, REVISE, SCALE, or STOP.

Key results: - On the RSICD cross-modal retrieval benchmark, an AutoResearch-generated staged idea (global alignment, text-guided local pooling, entity-position linking) improved mean Recall (mR) from 32.84 to 34.69 (+1.85 total), with only 5 audit-confirmed issue events versus 11 (R&D-Agent), 15 (AutoResearchClaw), 18 (Agent Laboratory), and 27 (The AI Scientist).

• On a 1024×1024 FP32 matrix-multiplication task, AutoResearch rejected an unstable pilot result, diagnosed a CPU-vs-wall-clock timing bug, and established a corrected reproducible baseline of 3.4 ms (626 GFLOPS, ~58× faster than the 200 ms target), recording 4 audit-confirmed issue events versus 5 (R&D-Agent), 5 (Agent Laboratory), 7 (AutoResearchClaw), and 8 (The AI Scientist).
• On three Kaggle benchmark-ML tasks, AutoResearch made evidence-conditioned decisions: Titanic accuracy improved from 0.822 to 0.843 (exceeding the 0.830 target, leading to scale-up); House Prices RMSLE improved from 0.2008 to 0.1251 (short of the 0.120 target, leading to continued revision); Disaster Tweets F1 improved from 0.763 to 0.805 (below the 0.835 target, leading to termination with the negative result retained).
• In a one-week (7×24 hour) run on a single server (dual Intel Xeon Platinum 8563C CPUs, 98 cores/196 threads, 8× NVIDIA L20 GPUs, 944 GiB memory), AutoResearch generated approximately 2584 candidate ideas, of which about 355 entered the experimental queue, leading to roughly 22 automatically executed experiments and approximately 14 empirically validated ideas.

Why it matters / caveats: The authors argue autonomous research should be judged not just by how much of the workflow is automated but by whether the process stays grounded from idea formation through experimental conclusion ("Insight In, Hallucination Out"), treating negative/inconclusive outcomes as valid research results rather than failures. Stated limitations: the current system still depends on the coverage of external signals, the quality of the accumulated domain knowledge, and the availability of explicit experimental criteria for verification; the authors propose future work feeding verified evidence and outcomes back into the knowledge state (Kt+1 = U(Kt, Et, Yt)) to create a continuously evolving research process.

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Problem: LLMs that are both structurally compressed (fewer parameters, modified architecture) and then quantized to 4 bits lose significant reasoning, math, coding, and long-context capability, and the standard recovery recipes (quantization-aware training, and quantization-aware distillation from a recovered checkpoint) are either operationally fragile or fundamentally capped because the only available full-precision "teacher" is itself a distillation-recovered approximation of the original model.

Method: The paper proposes Quantization-Aware Healing (QAH), which heals the compressed, 4-bit (MXFP4) student model by distilling directly from the original, uncompressed, full-size model MHP (via KL divergence on output logits, with straight-through-estimator MXFP4 fake-quantizers, temperature τ=1), rather than from the intermediate bfloat16 recovered checkpoint MBF16 used by standard quantization-aware distillation (QAD). It is evaluated on a two-stage GPT-OSS 120B→60B→MXFP4 pipeline (and a 20B→9B pipeline) using a tensor-network structural compression operator, trained on a Nemotron + SmolTalk 2 data mixture with FSDP2 on 8 nodes of H200 GPUs, using an offline top-K logits (k=100) and fused chunked-KL loss implementation to fit 32k-context training in a fixed memory budget, plus freezing of quantization-sensitive submodules (embeddings, layer norms, selected attention components). It is compared against a matched quantization-aware training (QAT) baseline that instead optimizes cross-entropy against hard labels.

Key results: - The QAH-healed 60B MXFP4 student matches or beats its own bfloat16 (60B) source on 7 of 9 benchmarks, with gains of +7.4 on AA-LCR (42.7 vs. 35.3), +5.6 on AIME 2025 (76.3 vs. 70.7), +2.7 on Aider (40.9 vs. 38.2), and +2.3 on τ2-bench (61.7 vs. 59.4); the two losses (MMLU-Pro, SciCode) are only 0.2 and 1.4 points.

• The 60B QAH student uses roughly 4× less weight memory and half the parameter count of the 120B teacher, yet slightly exceeds the 120B teacher on LiveCodeBench (66.5 vs. 66.0) and comes within 1.6 points on GPQA Diamond (67.4 vs. 69.0); largest residual gap is on AA-LCR (−7.3).
• On a 20B→9B pipeline, QAH reaches a comparable peak average score to QAT (54.9 vs. 54.6) but in about 100 steps versus roughly 700 for QAT (~7× fewer steps; same ~400-step pattern holds at 60B); QAT then collapses, losing nearly 19 points by step 1200 (54.6 to ~36), while QAH stays within about two points of peak through 1200 steps.
• Distributed training backend has a large effect: across an 11-run QAT sweep on the 120B student, the best DeepSpeed ZeRO-3 configuration plateaus at 65.15 on GPQA Diamond (3.5–14.2 points below target across the sweep) while FSDP2 reaches 73.74, an 8.6-point gap on GPQA Diamond, versus a released 120B MXFP4 target of 69.0.

Why it matters / caveats: QAH reframes the quantization stage as a second opportunity for teacher supervision rather than a lossy step to minimize, yielding a 4-bit model that is simultaneously cheaper to serve, lighter in memory, and at least as accurate as its bfloat16 source, and it was used to produce the open-weight Hypernova-60B release plus an internal client deployment. The authors explicitly note limitations: they did not run the direct head-to-head QAD-from-MBF16 baseline (their central claim of a "recovered-teacher ceiling" is well-motivated but not directly measured), all results are single runs on small-n benchmarks (e.g., AIME 2025 has only 30 problems) with no seed variance/confidence intervals, experiments cover only one model family (GPT-OSS MoE), one quantization format (MXFP4), and one data mixture, and the structural compression operator used is proprietary so transfer to other compression methods (layer pruning, SliceGPT, low-rank decomposition) is unverified.

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Problem: Successful execution experience from complex, interdependent LLM workflows is typically lost after a single run, forcing later models to rediscover strategies and failure modes from scratch, and it is unclear whether verifier-grounded execution experience offers advantages over static procedural guidance (Skills) under otherwise controlled conditions.

Method: The paper introduces LongWoF-Bench, 778 machine-verifiable long-workflow tasks (341 code generation, 127 agent-environment synthesis, 151 mathematical reasoning, 159 rule following), each defined as T = (S, E, Y, V) with a public specification, environment, deliverable space, and a private machine verifier. Reusable experience is built with the EvoMap framework: an Evolver component runs an execution–verification–refinement loop (GDIv2) where a producer model (Claude Opus 4.8) attempts a task, receives sanitized verifier feedback on failure, and revises until a verifier-confirmed trajectory is obtained within a bounded rollout budget; this trajectory is then distilled into a structured "Gene" (preserving strategies, prerequisite checks, boundary conditions, and corrections) and stored in EvoMap for reuse by the same or different consumer models. This is compared against No Context and against Skill (static procedural instructions) across seven consumer models from four families: Claude Opus 4.8, Claude Sonnet 4.6, Gemini 3.1 Flash-Lite Preview, Gemini 3.1 Pro Preview, MiniMax M3, Qwen3-Coder-30B-A3B-Instruct, and Qwen3.5-397B-A17B.

Key results: - On the 252 tasks with Opus-verified trajectories, average strict pass rate across 7 models rises from 41.0% (No Context) to 51.2% (Skill) to 62.9% (EvoMap Gene); Gene beats Skill for every model by 8.7–15.5 percentage points (e.g., Claude Opus 4.8: 63.9% → 79.4%).

• On the complementary 526 reference-distilled tasks (no verifier-confirmed Opus trajectory), Gene instead trails Skill for every model by 3.3–11.3 points, showing provenance, not compact representation, drives Gene utility.
• On the 180-task common-evolved set, Opus-authored Gene outperform Gemini-authored Gene for every consumer model by 4.4–11.7 percentage points.
• For Claude Opus, one-shot Gene reuse passes 200/252 tasks vs. Skill's 161/252 (39 more tasks) while using 723,480 vs. 803,099 solve-time tokens, a 9.9% reduction.
• Multi-round experience discovery (404 calls, 1,333,968 tokens) to solve all 252 tasks vs. one-shot Gene reuse (252 calls, 723,480 tokens) shows a 45.8% reduction in solve-time tokens, with the largest per-task token savings in code generation (55.8%) and agent-environment synthesis (46.8%).
• Gains are most consistent in agent-environment synthesis (+15.6 to +29.7 pp) and rule following (+2.1 to +22.9 pp); code generation is more model-dependent (three models show small regressions of 1.7–4.9 pp); mathematical reasoning shows a large gain for Opus (+40.0 pp) but ties or regressions for several other models.

Why it matters / caveats: The authors state this shows verified execution experience can be externalized, retained via EvoMap, and shared across model families to improve long-workflow completion without repeatedly paying the cost of experience discovery, though they note the provenance comparison (Opus-evolved vs. reference-distilled) uses different task subsets and so should be read as provenance-associated evidence rather than a same-task causal ablation, and Gene cannot fully compensate when a task's bottleneck is the consumer model's underlying reasoning capability (as seen in mathematical reasoning).

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Problem: Retrieval-augmented QA systems can silently change which answers they give to the same question after a corpus (index) expansion — even with the model, prompt, retrieval policy, evidence depth, and generation controls held fixed — and aggregate accuracy can hide this "accuracy-blind answer churn" because gains and losses cancel out.

Method: The authors introduce the Snapshot Compatibility Audit, which estimates "excess answer churn" (D̂) by subtracting same-snapshot repeat disagreement (two independent calls to the same corpus state) from cross-snapshot disagreement (calls to two different corpus states), using two co-primary similarity kernels: normalized-exact match and a blinded pairwise semantic-equivalence LLM judge. They instantiate the audit on a fixed single-turn retriever-generator built on the DeepResearchGym infrastructure over a FineWeb index, expanding one frozen nested shard prefix from n1 (one shard) to n7 (seven shards), with top-8 retrieved documents per query and the generator deepseek-v4-flash (tools off, independent singleton sessions, two repeats per question/scale). Inference uses a preregistered 50,000-draw whole-question bootstrap, and a post-hoc "repeat-stable semantic flip" diagnostic (Equation 7) identifies questions where both within-state repeats agree but all cross-state pairs disagree.

Key results:

• Preregistered 400-question Natural Questions (NQ) study: normalized-exact excess churn D̂ = 6.44 pp (LCB 4.56 pp) and semantic excess churn D̂ = 10.25 pp (LCB 7.69 pp), while exact-match (EM) accuracy changed by only −1.50 pp.
• Separately preregistered 200-question TriviaQA study: smaller but directionally consistent excess churn (3.00 pp exact, 2.125 pp semantic), while EM moved in the opposite direction (+1.25 pp).
• Post-hoc diagnostic: 40/400 NQ questions and 5/200 TriviaQA questions were strict repeat-stable semantic flips; the 40 NQ flips alone contributed 10.00 pp of the total 10.25 pp semantic churn.
• Outcome-blind 100-question NQ subset replication with a second generator/serving config (deepseek-v4-pro): semantic excess churn = 8.75 pp (exact = 7.25 pp) even as EM rose by 3.00 pp.
• Mean exact document-ID overlap in top-8 retrieval sets between n1 and n7 was only 1.19/8 (NQ) and 1.09/8 (TriviaQA), with 27.75%/29.50% zero-overlap rates and no question having an identical top-8 set, yet cross-scale semantic agreement remained 78.88% (NQ) and 94.63% (TriviaQA).
• Matched-repeat NQ transitions: 46/800 comparisons moved EM-match→EM-nonmatch and 34/800 the reverse (net −1.50 pp), but gross correctness flow was 80/800 (10.00%) and a further 155/800 (19.38%) moved between semantically different EM-nonmatches, invisible to binary accuracy.
• Cross-family semantic-judge audit (OpenAI gpt-5.6-sol vs. DeepSeek judge on 50 outcome-blind questions): 95.71% agreement, Cohen's κ = 0.855, with comparable churn estimates (9.50 pp vs. 11.00 pp).

Why it matters / caveats: The authors argue that retrieval-augmented system releases (index rebuilds, retriever swaps, chunking/deduplication changes) should be audited for answer-level compatibility alongside utility, since positive excess churn persisted across NQ, TriviaQA, and the replication regardless of whether EM went up, down, or barely moved. They explicitly caveat that the study covers only one frozen FineWeb shard path, one search service, and one generator family with two serving configurations, so it does not establish a universal scaling law, does not identify which specific document caused a given answer change, does not include human semantic validation, and answer changes are "not automatically regressions or harms" (e.g., one flip improved an UNKNOWN answer to a reference-matching one).

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Problem: Existing bidirectional RNA foundation models are pretrained with short context lengths (~1,024 tokens), forcing truncation/cropping of full-length mRNAs and preventing complete-transcript, single-nucleotide-resolution modeling.

Method: RIBOSPAN is a 1.61-billion-parameter, 32-layer pre-norm bidirectional Transformer encoder (model dimension 2,048, 32 attention heads, SwiGLU FFN, RoPE with rotary dim 64) using single-nucleotide tokenization and natively pretrained with masked language modeling (MLM) at a context length of up to 10,240 tokens, using attention-isolated sequence packing (via a customized Megatron-LM/Transformer Engine pipeline) to pack multiple RNAs per sequence without cross-sequence leakage. Pretraining proceeds in two stages: an initial 15% masking stage (RIBOSPAN-10K-15) followed by continued pretraining with 40% masking (RIBOSPAN-10K-40); 1,024-token baselines (RIBOSPAN-1K-15/1K-40) are trained identically for comparison. Building on the same frozen backbone, the authors add a conditional discrete-diffusion generation framework (inspired by MDLM) with AdaLN-Zero-conditioned diffusion blocks for multidimensionally conditioned full-length mRNA generation/redesign, including synonymous-codon diffusion that restricts CDS substitutions to synonymous codons.

Key results: - Pretraining corpus: 67.6M RNA sequences / 85.7B nucleotide tokens from RNAcentral v26.0, Ensembl release 115, and Ensembl Genomes release 62.

• At 10,240 tokens under 15% masking, RIBOSPAN-10K-15 achieves MLM loss 0.72417 vs. 0.98153 (RIBOSPAN-1K-15) and 1.15072 (AIDO.RNA-CDS) via extrapolation; global reconstruction accuracy at 10,240 nt is 0.94763 (10K-15) and 0.94517 (10K-40) vs. 0.91576 for AIDO.RNA-CDS.
• Under heavy 40% masking at 10,240 nt, RIBOSPAN-10K-40 reaches the best global reconstruction accuracy of 0.85887 (vs. 0.83769 for 10K-15, 0.80264 for 1K-40, and 0.77791 for AIDO.RNA-CDS).
• On the long-context representation benchmark at 10,240 nt, native 10K models (∆CS ≈0.406, Ccross ≈0.30) substantially outperform direct extrapolation baselines (∆CS 0.19–0.22, Ccross 0.70–0.74) while keeping distal diffusion low (Ddistal ≈0.0008–0.0012), whereas inference-time YaRN scaling restores ∆CS (~0.41–0.45) and Ccross (~0.32–0.36) but with much larger Ddistal (0.016–0.030).
• In frozen-representation RNA-type evaluation (89,955 sequences, 25 biotypes), RIBOSPAN-10K-15 achieves the highest Overall Biotype accuracy (0.898861) and purity (0.859254) among all evaluated models (RNA-FM, RiNALMo, AIDO.RNA-CDS, HydraRNA), and both 10K checkpoints achieve the best Long-RNA accuracy (~0.889–0.891) among all models.
• RNA-FM achieved the strongest performance on the Rfam family-homology subset, with RIBOSPAN remaining highly competitive (0.983818–0.983970 accuracy vs. 0.990485 for RNA-FM).

Why it matters / caveats: The authors state RIBOSPAN is the first billion-scale dense bidirectional Transformer RNA model combining single-nucleotide tokenization, dense self-attention in every layer, and native pretraining at full-transcript context lengths (10,240 nt), and that this establishes a versatile foundation for both RNA representation learning and full-transcript mRNA design; a caveat noted is that the complete mRNA design and reinforcement-learning post-training framework, including corresponding model checkpoints and biological/downstream evaluation, is left to a forthcoming journal publication rather than being reported here.

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Problem: Existing LLM attention acceleration methods apply numerical precision (e.g., INT8 quantization) uniformly per kernel invocation or attention stage, or select token connectivity via sparsity, leaving spatial precision routing over hardware-aligned score tiles unexplored within fused dense attention, so uniform low-precision attention loses long-context quality that a spatially adaptive approach could recover.

Method: TileMix is a tile-centric precision-routing kernel that partitions the L×L attention score matrix into hardware-aligned BLOCKM × BLOCKN score tiles and dispatches each tile group to either an FP16 or INT8 (Tensor Core MMA with INT32 accumulation) score-computation path within a single FlashAttention-style fused kernel, with both paths updating one shared FP16 online-softmax state (running maximum, normalizer, output accumulator). Routing decisions are given by a binary tile-group routing map R (instantiated via static, data-free structured templates such as align_sparse, bigbird, global, row_rand, and sptrans, at configurable INT8 coverage budgets), packed into compact 64-bit bitmasks per (KV head, query-tile row) for constant-time shift-and-mask lookup in the inner loop, with a scalable grouping factor g letting one routing bit govern multiple adjacent key tiles (BLOCKmask_N = g·BLOCKN) to keep metadata compact at long context lengths. The method is training-free and natively supports grouped-query attention (via KV-head mapping hk = floor(hq/(Hq/Hk))), variable-length batching (via cu_seqlens/prefix-sum metadata), and INT8 key/value caches; it was evaluated primarily on LLaMA 3.2 3B, with additional results on Vicuna-7B, Qwen-2-7B, and Qwen-2.5-7B.

Key results: - On LV-Eval long-context QA (LLaMA 3.2 3B), uniform INT8 ("One") often trails FP16 (e.g., dataset 3 at 16k: FP16 6.72 vs. One 4.45), while TileMix routing layouts (e.g., sptrans at 16k on dataset 3: 21.04–21.65) close or exceed this gap, and the sptrans layout at 16k factual recall recurs as a strong result across LLaMA and Qwen models at all coverage ratios.

• On prefill throughput (LLaMA 3.2 3B-Instruct, A100 40GB, batch size 8), at 4k tokens SpTrans75 reaches 31.80 K tokens/s vs. 14.33 K tokens/s for FlashAttention and 29.80 K tokens/s for uniform INT8 ("One"); FlashAttention and Torch baselines run out of memory (OOM) at 8k and 4k/8k tokens respectively, while TileMix configurations continue to run (e.g., "One" reaches 27.41 K tokens/s / 136.76 TOPS at 8k).
• On LongEval retrieval accuracy (3.1k–38.7k tokens), routing layout determines quality more than nominal INT8 coverage alone: row_rand and sptrans retain stronger accuracy as INT8 coverage rises to 75%, whereas align_sparse, band, and global retain more quality only under conservative (lower) coverage.
• Numerical-deviation analysis (mean absolute output deviation from Torch FP16 reference) shows deviation is small near 0% INT8 coverage and generally grows with coverage; at 8k tokens, deviation increases markedly between 5% and 10% coverage (from 8.34×10⁻⁴ to 6.32×10⁻³) and then stays roughly at that scale up to 25% coverage (6.84×10⁻³), indicating coverage acts as a practical numerical-control knob.

Why it matters / caveats: TileMix demonstrates that spatial precision routing over score tiles can recover long-context accuracy lost to uniform INT8 quantization while still improving prefill throughput over FP16, giving a controllable accuracy-efficiency frontier without retraining. The authors state the current implementation is limited to forward inference during long-context prefill with FP16/INT8 Tensor Core paths specifically on NVIDIA A100 GPUs, other numerical formats would require format-specific scale handling and kernel scheduling, and the evaluated routing policies are static (data-free) templates, though the kernel interface can in principle consume alternative static or adaptive routing policies.

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Problem: Federated ECG arrhythmia classification is hampered by limited client-side samples, imbalanced arrhythmia labels, and non-IID data across clients, requiring classifiers that are both communication-efficient and robust to cross-client distribution shifts.

Method: The paper benchmarks a hybrid quantum-inspired Kolmogorov–Arnold network (HQKAN) against an MLP baseline under federated averaging (FedAvg), built on the FLamby federated optimization pipeline. HQKAN pairs a fully connected encoder and decoder with a QKAN latent feature processor (forming an autoencoder-like architecture), where the QKAN uses DatA Re-Uploading ActivatioN (DARUAN) trainable single-qubit circuits as edge functions in place of fixed spline activations; it is implemented via the GPU-efficient FlashQKAN framework in PyTorch with fused operators and cuTe DSL block tiling. Both models are trained for R=30 communication rounds with E=5 local epochs (AdamW, lr=1e-3, weight decay=1e-4, batch size=128, inverse-class-frequency-weighted cross-entropy) across K∈{8,16,32} clients under IID and Dirichlet non-IID (α=0.3 main setting, swept over α∈{0.1,0.3,0.5,1,1000}) partitions, on five-class MIT-BIH and three-class INCART ECG heartbeat classification.

Key results: - HQKAN uses 11,581 trainable parameters vs. 18,485 for MLP on MIT-BIH (37.35% reduction) and 15,147 vs. 27,443 on INCART (44.81% reduction); per-round communication cost is reduced by 24.89% (MIT-BIH) and 36.41% (INCART).

• At 32 clients under non-IID partitions, HQKAN achieves macro-F1 of 0.761 vs. 0.698 for MLP on MIT-BIH (Brier score 0.094 vs. 0.121), and macro-F1 of 0.850 vs. 0.838 on INCART (Brier score 0.032 vs. 0.040).
• On MIT-BIH IID, HQKAN's macro-F1 advantage over MLP grows from 0.013 (8 clients) to 0.054 (32 clients); on INCART IID the gap grows from 0.023 to 0.030.
• Minority-class gains under non-IID MIT-BIH: HQKAN's mean sensitivity exceeds MLP's by 0.147 (class S), 0.077 (class V), and 0.073 (class F) at 32 clients; on MIT-BIH IID, class F PPV is 0.239 (HQKAN) vs. 0.147 (MLP).
• Across all tested Dirichlet concentrations (Hellinger-distance-summarized heterogeneity) at 32 clients, HQKAN attains higher mean AUROC and AUPRC than MLP on both datasets, with the margin widening at the largest heterogeneity levels, especially for AUPRC.

Why it matters / caveats: The authors conclude that robustness to client heterogeneity need not trade off against model or communication efficiency, positioning HQKAN as a compact, communication-efficient, and robust alternative to MLP for privacy-aware federated learning on biosignal data; however, minority-class performance trade-offs are noted (e.g., HQKAN sometimes shows lower sensitivity despite higher PPV, such as class F on MIT-BIH IID and class S on INCART), indicating gains depend on class, metric, and partition regime rather than being uniform.

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Problem: No public instruction-tuning or benchmark datasets exist for industrial technical reports, whose heterogeneous structure (dense prose, specifications, and tables) makes them hard to index and reason over with standard retrieval and QA pipelines.

Method: The authors build "Industrial-Instruction," an end-to-end pipeline that (1) extracts text and tables from 906 publicly available Panasonic PDF documents (7,525 pages) using the vision-language OCR model Dots.OCR, (2) builds a semantic retrieval index with the EmbeddingGemma (300M-parameter, Gemma3-derived) embedding model and FAISS, and (3) synthesizes multiple-choice QA pairs grounded in retrieved evidence across five query–document relationship scenarios (r0–r4: Useless Document, Single-Document Support, Multi-Document Support, Single-Document Answer, Multi-Document Answer), using SensorIQ-style instructions from IBM as simulated-instruction templates. The pipeline was run twice with identical prompts/scenarios to produce two parallel dataset versions — one generated by the open-weight Qwen3-30B-A3B-Instruct model and one by the closed API model Claude-Opus-4.6 — followed by rule-based filters (valid-option structure, options embedded in question text, valid answer-response format). Small open LLMs (<10B parameters, primarily Qwen3-4B-Instruct) are then evaluated and fine-tuned (via LoRA and full fine-tuning) on the resulting data.

Key results: - Qwen3-30B-A3B-Instruct generation produced 23,910 raw Q&A pairs; after filtering, ~13,557 remained (about 43% removed), split into 12,557 training and 1,000 benchmark samples.

• Claude-Opus-4.6 generation produced 26,395 raw Q&A pairs with only 143 (0.5%) removed by the same filters, yielding 25,252 training and 1,000 benchmark samples — a much cleaner raw corpus.
• LoRA fine-tuning (ranks 8/16/32/64) produced negligible change (Set-Match Accuracy stayed ~28.2–28.7%), while full fine-tuning on the Qwen-generated dataset raised Set-Match Accuracy from 28.5% to 42.0%, F1 from 46.57% to 63.48%, and Jaccard from 41.57% to 57.95% (with RAG).
• Full fine-tuning on the Claude-generated dataset raised Set-Match Accuracy from 40.9% to 56.4%, F1 from 58.55% to 72.66%, and Jaccard from 54.00% to 68.88% (with RAG) — roughly a 15-point gain vs. ~13.5 points for the Qwen-generated data (though on different held-out splits, so not strictly comparable).
• Generating the dataset cost ~$3.2 in local compute (1h43m on a Pro 6000 WS) for Qwen3-30B-A3B-Instruct versus ~$330 in API usage for Claude-Opus-4.6 (~100x more expensive).
• MMLU accuracy dropped only 0.05 points overall for the model fine-tuned on Claude-generated data (72.13%→72.08%) versus a 1.26-point drop for the Qwen-generated data (72.13%→70.87%), with the Qwen-fine-tuned model showing a ~10.7-point drop on moral_scenarios specifically.
• Baseline (non-fine-tuned) models on the Panasonic benchmark: Qwen-4B-Instruct 28.5% Set-Match Accuracy/46.65% F1, Phi-3-mini-4k-Instruct 17.5%/31.27%, RAG-Instruct-Llama3-8B only 0.70%/0.90%.
• On FailureSensorIQ, no model (base or fine-tuned Qwen variants) answered any perturbed question correctly (AccPerIBM = 0%), while RAG-Instruct-Llama3-8B scored 33% on that metric despite performing far worse (3–5x lower) on the Panasonic benchmark.

Why it matters / caveats: The work shows small (<10B-parameter) open models can be substantially improved on real industrial QA via full fine-tuning on synthetically generated, retrieval-grounded data, and that open-weight generator models (Qwen3-30B-A3B-Instruct) remain highly cost-effective relative to frontier API models despite producing a noisier raw corpus. The authors explicitly note limitations: the two fine-tuning comparisons use different held-out test splits so improvement magnitudes are "indicative rather than strictly controlled"; all evaluated models totally failed on perturbed/rephrased FailureSensorIQ questions (a brittleness the current pipeline does not address, since it does not generate paraphrased/adversarial variants); and the study used only text-based (not multimodal/vision-language) models, discarding extracted images.

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Problem: The paper asks how far generative world models have actually progressed toward being true, rigorous simulators (replacements for physics engines, game engines, and RL environments) rather than just visually convincing generators.

Method: The authors conduct a systematic, capability-based literature audit using an external, route-independent yardstick derived from traditional simulators (physics engines like MuJoCo/Isaac Sim/PyBullet, game engines like Unreal/Unity, and RL environments like Atari ALE/CARLA/DMControl): eight capabilities — asset construction (C1), physics engine (C2), interaction (C3), controllability (C4), stability (C5), state feedback (C6), diversity (C7), and evaluation metrics (C8). They curate 200 papers (2018–June 2026) via multi-source search (Google Scholar, arXiv, DBLP, Crossref) plus citation-network expansion, classify 163 "implementation papers" into six technical families (latent-dynamics/latent-action, autoregressive, diffusion, JEPA-predictive, explicit 3D/4D reconstruction, occupancy-centric), and trace three main technical routes (latent dynamics, video generation, joint-embedding prediction) plus their 2024–2026 convergence trend. For state feedback specifically, they perform a five-variable audit (B1 ego info, B2 sensor output, B3 task/reward signal, B4 runtime entity/physics annotations, B5 closed-loop interaction) across all 163 implementation papers, reporting present/absent/unresolved counts.

Key results: - Controllability (C4) and interaction (C3)/stability (C5) are flagged as relative strengths, appearing as a principal contribution in 125, 80, and 80 papers respectively (of 200); asset construction (C1, 19.0%/38 papers), physics engine (C2, 17%), and state feedback (C6, 22.5%/45 papers) are structural gaps; diversity (23%) and evaluation (25.5%, 18 benchmark papers) are neutral.

• State-feedback audit (163 implementation papers): B1 (ego info) present in 65; B2 (sensor output) present in 45; B3 (reward/termination) present in 20; B4 (runtime queryable entity/physics annotations) present in only 6; B5 (closed-loop interaction) present in 87.
• Of the 200-paper corpus, 72 papers are formally published (22 at ICML/NeurIPS/ICLR, 20 at CVPR/ICCV/ECCV, 6 at CoRL/ICRA/RSS, 6 at AAAI, 3 in Nature, 15 elsewhere) while 128 remain arXiv preprints, concentrated in 2025–2026.
• GameNGen achieves ~20 FPS real-time interaction with only 58–60% of human subjects able to distinguish real vs. generated DOOM screenshots; Matrix-Game series reaches up to 720p at ~40 FPS.
• V-JEPA 2 (1.2B-parameter ViT, pretrained on 1M+ hours of internet video plus 62 hours of unlabelled robot fine-tuning) achieves zero-shot Franka manipulation transfer; V-JEPA 2-AC needs ~16 seconds per action for latent-space planning versus ~4 minutes for comparable pixel-generation planning (roughly a 15x speed advantage).
• UWM-JEPA reaches 0.77 accuracy on a five-step forward-simulation task under occluded/blind rollouts, versus 0.53 for a parameter-matched LSTM-JEPA.

Why it matters / caveats: The authors conclude world models can achieve functional substitution for traditional simulators only "under restricted conditions," remaining "a critical step away" in strict sense due to lack of formal physical guarantees, sparse/unstructured state feedback, and unproven long-horizon reproducibility (the corpus provides little comparable evidence on seed control, deterministic execution, or repeat-run variance). They propose six future research directions — formalized physics, a unified action interface, first-class state feedback, long-horizon stability, downstream-utility evaluation, and cross-route hybridization — as an actionable roadmap, and caution that combining routes' differing optimization objectives (pixel loss, latent-space energy, policy return) is a genuine unsolved obstacle to fusion.

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Problem: Robot imitation-learning policies lack a common answer to what the basic unit of the top-level policy sequence should represent (heterogeneous per-timestep inputs like multi-view images, proprioception, and language are organized inconsistently across architectures — via multiple modality tokens, recurrence, or retrieval), and the paper studies "time-first" organization as a fix: using the policy timestep itself, resolved into one token, as the sequence unit.

Method: WorldToken decomposes the policy into three sequential modules: a within-timestep multimodal encoder Eθ that fuses multi-view images, proprioception, and task conditioning (via learned readout tokens, R=4) into a single fixed-width "world token" zt per policy timestep; a causal temporal Transformer Tϕ, instantiated as a Qwen2-decoder-architecture backbone trained from scratch with 1D RoPE and causal self-attention, that contextualizes the world-token sequence z1...zt into a history representation ht; and a DiT (Diffusion Transformer) action head that uses adaLN-Zero conditioning on ht and diffusion step k to denoise Gaussian noise into an H-step action chunk via DDPM sampling, executing only the first Hexec actions before replanning. The full policy is trained end-to-end from scratch (only the CLIP text encoder for task conditioning is frozen/pretrained), and is evaluated at multiple parameter scales (44.3M to 1.49B) on RoboCasa and on RMBench Blocks Ranking.

Key results: - On 23 RoboCasa tasks with 2,900 demonstrations/task, the 85.3M-parameter policy reaches 59.45% mean closed-loop success rate (best individual run 60.1–62.0%), within the ~50–79% range reported for billion-scale pretrained RoboCasa systems.

• At 300 demonstrations/task, WorldToken (85.3M params) reaches 46.83% SR vs. 31.28% for a from-scratch BC-Transformer baseline (a 12–16 percentage-point gain).
• Across a full 5×5×2 sweep (dataset size × model size × seed, 50 policies, 172,500 closed-loop episodes), holdout RMSE decreases and closed-loop SR improves in all 40 paired data-size comparisons; increasing D from 50 to 2,900 reduces RMSE by 47.0–56.8% and raises SR by 32.7–39.3 percentage points, with diminishing SR gains at the largest sizes (+3.39pp average from D=1000 to D=2900 despite RMSE still improving 17.10%).
• RMSE improvement from added model capacity is concentrated between 44.3M and 218.8M parameters (reliable gains), with no consistent further RMSE reduction beyond 218.8M; fitted power-law exponents for RMSE vs. data range from 0.151 to 0.211 (R²=0.990–0.999).
• Truncating visible history to 1–2 policy timesteps at inference lowers closed-loop SR for all 50 trained policies (minimum drops of 3.5pp at 1 step and 1.4pp at 2 steps), while ~5 visible timesteps already recovers most of the SR (47/50 policies within 2pp of the C=10 result); separately trained short-context policies (C=1 or C=2) largely recover the lost performance (e.g., 46.75%/47.68% SR vs. 27.91%/27.83% when a C=10-trained policy is truncated to C=1).
• On RMBench Blocks Ranking, reducing visible history from 608 to 32 world tokens (145.9s to 7.68s) lowers evaluator success from 95% to 28% (monotonic: 95%, 92%, 59%, 38%, 28% for C=608, 288, 128, 64, 32), with failures concentrated in multi-swap episodes; in an exploratory extended rollout, one trajectory completes 31 correctly ordered swaps (26 after the context began sliding), with its last correct swap at 856.44 seconds — over 5x the 145.92-second context span — despite training demonstrations containing at most 5 swaps.

Why it matters / caveats: The authors frame time-first organization as a physically interpretable "interface" for studying embodied sequence modeling — separating within-timestep encoding, temporal modeling, and action generation so architectural changes can be attributed more cleanly — rather than a proven superior design; they explicitly state the results do not establish superiority over alternative sequence organizations or isolate which components drive performance. Stated limitations: evidence is confined to simulation and action-only imitation learning, the scaling study covers only one WorldToken family, the extended-context evidence rests on a single long-horizon case study (Blocks Ranking), and the work does not test real-robot deployment, explicit action history, predictive objectives, or system-level efficiency.

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Problem: Deep face recognition (FR) models achieve near-saturated accuracy but remain opaque, giving practitioners a similarity score with no way to ask which semantic attributes it relied upon.

Method: EXPL-FR trains a single lightweight adapter (a 4-layer MLP, bias-free linear + BatchNorm + GELU blocks then a linear output, ~1.05M parameters at 512→512 or 1.18M at 768→512) that maps a frozen vision-language model's (VLM) image embeddings onto a frozen FR encoder's embedding space, using a cosine alignment loss (Eq. 2) trained only on paired face images (never text) from WebFace4M with a 10% identity-disjoint holdout. Because the VLM's image and text encoders share one pretrained space, the same frozen adapter is applied zero-shot to text prompts (978 attribute prompts across 22 categories) to produce FR-space "anchors," and a face's cosine similarities to these anchors form its semantic signature. A label-free detectability measure (comparing AUC of a mean-difference detector in VLM space vs. adapter-mapped FR space) selects the top-100 most identity-discriminating attributes as the deployed signature, and the same signatures support identity-level, per-image, and differential (genuine/imposter/morph) explanations plus a three-tier attribute auditing benchmark (labeled, VLM-proxy, and fully prompt-driven).

Key results: - Cross-modal alignment/faithfulness (AdaFace ViT-B/WebFace4M + CLIP ViT-B/16): FR self-verification upper bound 97.44% mean accuracy vs. unaligned cross-encoder chance-level 50.29%; aligned-VLM self-verification rises from 82.33% (raw CLIP) to 92.58% after adapting (+10.25 points), and SigLIP rises from 72.77% to 84.78% (+12.01 points).

• Vocabulary-projection faithfulness: similarities to the 978 prompts in native CLIP space carry almost no identity information (51.98% mean), but the same prompts mapped through the image-trained adapter reach 71.66% (+19.68 points), isolating the cross-modal transfer contribution.
• Generality across 4 FR targets/2 VLMs: aligned-VLM self-verification stays within 0.71 points (91.88-92.59%) across targets, while vocabulary-projection faithfulness varies more, e.g., 75.18% for ResNet-100/WebFace4M vs. 69.57% for ResNet-100/MS1MV2 (5.61-point spread).
• Semantic signature (m=100) beats the full 978-prompt vocabulary on identity separability (genuine/imposter AUC), e.g., 0.931 vs. 0.910 for the primary model, and outperforms random/bottom-m subsets.
• Label-free audits validate against real behavior: RFW ethnicity-vs-error model ranking gives mean Kendall τ = 0.92 (min 0.67) under all three supervision settings (joint p = 1.2×10⁻⁵); GAN-Control sensitivity-vs-EER rank correlation is Spearman ρ = 0.90/0.83/0.95 for labeled/VLM-proxy/prompt-only settings (primary target, n=8, p ≤ 7.7×10⁻³); CelebA cross-check against labels gives Spearman ρ = 0.64 (p=1.0×10⁻⁵, n=40) for label-free vs. labeled dependence rankings.
• The FR-space vocabulary projection remains 25.78 points below the FR self-verification upper bound (71.66% vs. 97.44%), and 8-way attribution accuracy on GAN-Control drops from 82-90% (labeled) to 33-34% (VLM-proxy) to 16-19% (prompt-only, chance = 12.5%).

Why it matters / caveats: EXPL-FR needs no access to the FR model's internals (post-hoc, black-box) and, using only prompts and unlabeled images, can rank FR models by real per-ethnicity bias (RFW) and rank controlled attribute changes by true verification cost, reproducing analyses that previously required per-image labels or a controllable generator. The authors state explicit limitations: not all identity cues are nameable via language (a persistent gap to the FR upper bound) and prompts are not disentangled so readings are directional; every construction inherits what the VLM can rank on an image, and for concepts near the edge of the VLM's range (notably pose and illumination) the audit still returns values that look like findings but are inconclusive, a blind spot the two-space comparison flags only imperfectly; and the detectability measure is scored against the VLM's own pseudo-labels rather than absolute ground truth.

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Problem: Face presentation attack detection (PAD) is conventionally treated as inherently face-dependent, and the paper questions whether transferable PAD representations can instead be learned without using any face images during downstream training.

Method: The authors build TPO, a controlled face-free PAD dataset of 12,480 bona fide, print, and replay presentations of tomatoes, potatoes, and onions (78 object identities, 26 specimens per species), captured with a Microsoft Surface tablet and Samsung Galaxy smartphone under a factorial protocol (four viewpoints, close/far scale, matched/mismatched devices) that mirrors conventional face PAD acquisition. The main detector follows the FoundPAD recipe: a frozen CLIP ViT-B/16 image encoder adapted with rank-stabilized LoRA (r=8, alpha=8, dropout 0.4) on the query/value projections of all 12 attention blocks, plus a linear two-class head on the L2-normalized embedding, totaling about 0.30M trainable parameters (with a corrected CLIP-native normalization instead of ImageNet normalization). Models are trained on TPO, SynthASpoof, or real face datasets (MSU-MFSD, CASIA-FASD, Idiap Replay-Attack, OULU-NPU) under a fixed common budget of about 11,000 optimizer updates (~530,000 sampled image views, batch size 48) and evaluated with a strict cross-dataset protocol (no train/test overlap).

Key results: - A detector trained only on TPO (no faces) reaches 92.70% average AUC and 14.15% HTER across the four standard face PAD benchmarks (MCIO), versus 81.02% AUC for training on SynthASpoof synthetic faces and 67.81% AUC for an architecture-matched ImageNet-21k ViT-B/16 trained on TPO.

• Reverse transfer (face-trained models tested on TPO) ranges from 58.89% to 89.88% AUC depending on the single face source, consistently above the CLIP zero-shot baseline (67.72% AUC on TPO, ~56.11% average AUC on MCIO).
• Replacing part of a fixed single-source face training budget with TPO raises average AUC from 89.33% to 92.55% (HTER 17.54% to 13.97%) across 12 cross-dataset protocols; in multi-source (double/triple face dataset) regimes it raises AUC from 92.11% to 96.96% (HTER 14.72% to 7.84%).
• Restricting TPO to a single attack type lowers average AUC from 92.70% to 86.14% (print only) or 83.97% (replay only); single vegetable categories still transfer well (onions alone: 91.78% AUC), and using only 10% of frames barely changes performance (92.97% AUC, 13.56% HTER), indicating attack/object diversity matters more than sample volume.

Why it matters / caveats: The authors argue face PAD is better understood as recapture-artifact detection rather than face-specific learning, opening a path to privacy-preserving, consent-free, and demographically bias-free PAD data collection (though the fairness claim remains theoretical and untested here). They explicitly limit their conclusions to print and replay attacks in the visible spectrum, note CLIP's pretraining data may itself include faces (so they claim reduced rather than eliminated face data use), and flag that attacks depending on 3D object geometry (e.g., masks) or other modalities (depth, IR) remain open questions.