arXiv subjects

Yangze Liu

Publications and source records attributed to Yangze Liu.

8 recordsLinked to original sources

arXiv2026

Silent Instrument Errors Reorder Agent Leaderboards

On a public agent leaderboard, a general-purpose agent trails a scaffold built for an airline customer-service benchmark by 13 points on the tasks that touch its database, and a reader could conclude that generality costs accuracy. The gap comes from the grader. The general agent often ends its conversations in a way that never triggers grading, so only about half of its episodes were scored and the rest were stored as failures. Grading the ungraded half under the benchmark's own rule closes the pooled gap, without rerunning any agent. We audit two carefully maintained public leaderboards, HAL and tau2-bench, from their published artifacts alone and find three more instrument errors. A cost column counts nested model calls twice, unevenly across rows. Archived trajectories record grader-written actions as agent actions. Re-grading saved trajectories under a newer evaluator is itself a new measurement: a correct and announced fix reorders a leaderboard, and a mode check that misreads four files collapses their scores by 59 to 82 points while printing no error. Each produced a plausible number, and the HAL maintainers confirmed their three within five weeks. Together the cases show that the infrastructure of agent evaluation, meaning the code that grades, logs, replays and versions an evaluation, is part of the measurement and fails silently, so scores and orderings can move with no visible sign. These failure modes follow from how agent evaluation pipelines are built, and those pipelines change as fast as the agents they measure, so we expect more of them elsewhere. We propose cheap checks that expose the instrument: report the graded fraction, aggregate cost from root spans, tag the provenance of every recorded action, and pin evaluator versions with a published re-grade diff.

cs.AI↗

arXiv2026

Useful to Whom? The Easy-versus-Coverage Boundary Moves with the Learner

Is the same data equally useful to every learner? The question is whether the value of a training sample belongs to the sample or arises in its interaction with the learner. We test it with a selection experiment. Under a per-class budget, two kinds of samples compete for the slots: easy samples, which a short training run learns first, and coverage samples, which spread over the class in feature space. Easy samples win at small budgets and coverage samples at large ones, and the budget at which the winner flips, the crossover m0, can be measured. We ask whether m0 is set by the data or by the learner. To separate the two, we freeze the selected subsets and change only the learner that trains on them. On low-resolution ImageNet-100, doubling the width of a ResNet-18 moves the crossover from 57 to 85 samples per class on the same subsets. Enlarging the input grid from 32 to 64 pixels at fixed image information moves it from 85 to 57, and a single stride change reproduces or removes this shift. The grid shift shrinks as width grows. Under the native ImageNet-1k protocol, a 4x range of width moves the boundary by at most a few samples per class. On a Vision Transformer, coverage wins at every measured budget, even with easy subsets that work on the convolutional learner. The budget at which one kind of sample stops being the more useful kind therefore belongs to the learner, and the preferred regime of a selection strategy has to be read against the learner that will use the data.

cs.LG↗

arXiv2026

Asking Earns Nothing: Scoring the Decision to Act in BFCL Multi-Turn

An agent that lacks the information it needs should ask rather than act, and the task definitions of agent leaderboards say so. BFCL multi-turn builds two of its four categories around a turn on which the model is supposed to ask, and its scorer never looks at that turn: the gold trajectory there is empty, the checker skips it, and the scripted user cannot answer, so asking earns nothing, guessing costs nothing on that turn, and asking twice loses the item. The benchmark also contains the control experiment for that decision. A should-ask item is a base item with one piece of information removed from one turn, so the same request appears twice at the same turn index, once complete and once not: on the first the model should make the call that changes the world, on the second it should ask. We score one decision per pair, whether the model attempted a world-changing call on that turn, read off the stored trajectories with no LLM judge; acting always and asking always both score 50. On the 223 pairs that pose this decision, gpt-5.4 attempts the call on 83.4% of the complete turns and holds back on 78.0% of the incomplete ones, the best decision accuracy of seven models at 80.7%; on the same items the official score ranks it sixth and puts first a model that lands in the middle here. One added line telling gpt-5.4 not to ask pushes it toward acting on both sides of the pair, so its decision accuracy shows no detectable change, while its official score rises by 13.5 to 23.5 points on the two should-ask categories and on the base twins; the opposite line, telling gemma-4-31B-it to ask first, improves its decision by 4.5 points and gains no official score. The score moves with the push toward action, not with the decision. We release the pairs, a turn-level scorer that runs on any BFCL output directory without an API key, and 31 manually verified bad items.

cs.AI↗

arXiv2026

What Does a Harness Buy? Tokens, Mostly

A coding agent is a language model wrapped in a harness: the system prompt, the tool set, and the context management that turn a chat model into something that can work inside a repository. Production harnesses ship releases daily, vendors advertise pass-rate gains from harness changes, and leaderboards mix harnesses freely. What is rarely measured is how much the harness itself moves the score when the model is held fixed. We run five models through three production harnesses, Claude Code, mini-SWE-agent, and OpenCode, on SWE-bench Verified, and rerun the same configurations to calibrate how much a score moves when nothing changes but the run. On 447 tasks and the two models we ran there, Claude Code and mini-SWE-agent, the heaviest and the lightest harness, are equivalent within five points. On a 45-task hard subset and five models, swapping the harness flips as many tasks as rerunning the same harness, 13% in both cases, and the tasks a harness wins in one run are not the tasks it wins in the next. The one harness effect that clears the noise is a loss, not a gain: OpenCode trails by up to 9 points on the large pool, and on one model half of that gap sits in runs its output cap cut short. What the harness does decide is the bill. With the same model, the same tasks, and one price list, cost per task differs by up to 3x across harnesses. The gap is set at the first call, by the preamble of system prompt and tool schemas each harness sends with every step, and scaled by the number of steps; per-step growth and per-call tool output differ far less. The provider's price for cached input scales the bill and does not reorder it. The rerun data also give the resolution a harness comparison needs: at the discordance we observe, 45 tasks catch a 13-point gap only half the time and no gap with 80% power, and 447 tasks resolve 5 points, still coarser than the gains many harness changes claim.

cs.AI↗

arXiv2026

A Dominant Supplier Slows Recursive Drift More Than It Steers It

More and more of the text future language models learn from is written by a few of today's models. If one supplier writes most of a shared corpus, does it pull the models trained on it toward its own writing, or change how fast they drift? We retrain eight open models from their base weights on a shared pool of each other's text for five generations, varying the part written by one model, Phi-2, from an equal share to 90%. The models drift together toward a style with fewer function words, and none starts repeating itself. No share of Phi-2 brings the other models closer to its text than the equal share does. We split each ecosystem's separation from the equal-share one into a delay along its route and a departure from that route, both counted beyond the difference between two equal-share runs. With Phi-2 at 90%, delay outweighs departure 72 to 28 and 64 to 36 in two runs, and the ecosystem falls 2.7 and 2.5 generations behind. With Phi-2 at half the pool the two parts are about equal. When SmolLM2 or Qwen3-1.7B writes half instead, the ecosystem slows less or not at all. The departure leans toward Phi-2 more as its share grows, but more than toward every other model only at 90%. Human text filling a quarter or half of the pool slows the models along the same route.

cs.AI↗

arXiv2026

Break Step: Recursive Training Resonates with Replayed Sampling Noise

How fast does a language model degrade when trained on its own outputs? Theory traces it to gradually accumulating errors, while experiments report repeated phrases within ten generations. Under a fixed sampling seed in vLLM, the fast loss of lexical diversity comes from the sampler. When vLLM serves a batch from one seeded sampling configuration, every request receives the same random draws, and a fixed seed replays them every generation. Fine-tuning raises the tokens that won, and the replayed draws let them win by more. Sharing across requests and replay across generations matter only together. Remove either one, by changing the shared seed every generation or by giving each request its own seed that repeats every generation, and the unique-4-gram fraction of two StableLM checkpoints stays near its starting value of about 0.98 through generation 3. Keep both, and the replayed shared seed takes seven checkpoints from five families to between 0.045 and 0.38 by then. Three generations of replay write the favoured phrases into the weights: decoded with one seed per request, the generation-3 weights of the replayed StableLM-2-1.6B chain recover most of their diversity, yet the phrase that filled every sample under the shared seed still opens 46% of them. Without replay, five checkpoints drift slowly, consistent with the gradual accumulation that theory describes, and three turn incoherent though their diversity scores stay high. One peer-reviewed model-collapse pipeline that fine-tunes Gemma-2-27B samples identical prompts under one seeded configuration, and three quarters of the rows it released for one iteration repeat nearly as often as one such batch copies them. A seed per request restores the fresh sample that stability analyses assume.

cs.CL↗

arXiv2026

Are Coreset Selection Methods Worth Their Cost?

Coreset selection picks a representative subset of the labeled training set to make training cheaper. However, it is usually evaluated by downstream accuracy at a fixed subset size, ignoring both the time spent selecting the subset and the training recipe behind each reported number. We introduce an end-to-end benchmark that standardizes downstream training and charges selection and training to the same auditable wall-clock budget, spanning 4 datasets from CIFAR-10 to ImageNet-1K, 11 selectors, 5 fractions, and 3 seeds, with over 1,500 released runs. Repeated-sampling work has shown that budget-aware evaluation already favors random strategies. Our two budget studies test whether that verdict survives when every selector is granted its most favorable operating point. Across eight wall-clock budget anchors on each of CIFAR-10 and Tiny ImageNet, no anchor is won by a sophisticated selector: every winner is class-balanced random sampling, repeated random sampling, or full-data training. In fixed-budget duels on ImageNet-1K, training on all data for fewer epochs beats every selection strategy we probe while also costing the least. A per-dataset cost audit shows that selection cost is dominated at every scale by a fixed full-dataset scan, so it cannot be amortized away by selecting a smaller fraction, and its absolute size does not extrapolate from one dataset to another. We further quantify when selection does pay back through subset reuse, and document 9 correctness fixes to a widely used codebase, one of which shifts a standard Herding baseline by nearly 6 points. Selection time is not free preprocessing, and an evaluation that ignores it measures the wrong quantity.

cs.LG↗

arXiv2026

OpenClawBench: Benchmarking Process-side Anomalies in Real-world Agent Execution Trajectories

Task success can hide process anomalies in real-world agent executions. An agent may pass the final task oracle while still accumulating unresolved ambiguity, unsafe external writes, ignored errors, weakly grounded commitments, or capability-boundary overcommitment. We study this mismatch as the Outcome-Process Gap and introduce OpenClawBench, a large-scale dataset for measuring and supervising process-side anomalies in real agent execution processes. OpenClawBench is built from BFCL-driven OpenClaw sessions produced by 6 source models and contains 31,264 annotated trajectories. It aligns task-oracle outcomes with structured process evidence. FullTax converts the aligned trajectories into structured anomaly supervision: binary labels, supporting evidence, onset/span localization, severity, recoverability, and a 5-class anomaly taxonomy. Using OpenClawBench, we make the Outcome-Process Gap measurable. Among 31,135 oracle-passing executions, 2,904 are still labeled process-anomalous under FullTax. These results show that success-only evaluation misses a concrete class of process-side failures in real agent executions. A LoRA-fine-tuned Gemma 3 12B detector trained on the high-confidence FullTax supervised pool reaches binary F1=0.729 on the cleaner-labels held-out test split. Together, OpenClawBench turns real agent execution logs into auditable and reusable supervision for studying, diagnosing, and operationally monitoring runtime agent reliability.

cs.AI↗