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arxiv: 2607.05316 · v1 · pith:6KTCEUN5 · submitted 2026-07-06 · cs.CL · cs.LG

How Much is Left? LLMs Linearly Encode Their Remaining Output Length

Mohamed Amine Merzouk , Dmitri Carpov , Mirko Bronzi , Damiano Fornasiere , Adam Oberman This is my paper

Reviewed by Pith T0 review T1 audit T2 compute T3 formal T4 kernel 2026-07-07 17:43 UTCglm-5.2pith:6KTCEUN5record.jsonopen to challenge →

classification cs.CL cs.LG
keywords lengthoutputcompletionsdatasetsdecodableestimateevidencehidden
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The pith

LLMs linearly encode how many tokens they have left to generate

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

This paper asks whether large language models carry an internal estimate of how much of their response remains to be written, or whether response-length consistency is merely a byproduct of token-by-token decoding. Using minimal linear probes trained on frozen hidden states of three 7-8B parameter models across seven datasets, the authors find three converging pieces of evidence that the model's residual stream contains a plan-like representation of remaining output length. First, total response length is linearly decodable from the prompt's final hidden state alone, before any output token is emitted. Second, probe directions trained on natural-language datasets transfer broadly to other datasets including controlled synthetic ones the probe never saw, while the reverse transfer fails -- an asymmetry the authors interpret as natural-language training recovering a general length-tracking direction rather than memorizing a dataset-specific marginal. Third, on curated examples where the model retracts and restarts a partial solution (e.g., emitting 'Wait, let me try again'), the probe's per-position estimate of remaining length jumps upward, a directional update no position-only predictor can reproduce. The authors frame this as approximate estimation of remaining generation length, distinct from exact-counting impossibility results for transformers, and explicitly note that decodability does not prove the model causally uses this signal.

Core claim

The residual stream of an instruction-tuned LLM contains a linearly decodable estimate of how many tokens of output remain, readable from the prompt's last hidden state before generation begins, transferring across datasets with different length distributions, and updating directionally upward when the model retracts and restarts a partial solution. The central object is the Remaining Count Probe -- a single linear layer with no nonlinearity that regresses on the residual-stream activation at each completion position to predict the remaining token count. The asymmetry in cross-dataset transfer (natural-language probes generalize to synthetic data but not vice versa) is itself a key finding,,

What carries the argument

A linear probe (single linear layer, no nonlinearity) trained on frozen residual-stream hidden states to predict remaining token count at each generation position. Three variants are compared: the Remaining Count Probe (reads hidden states at every position), a constant-median statistical baseline (dataset median at every position), and a Completion Length Probe (trained only on the prompt's last hidden state, then decremented by position). The cross-dataset transfer matrix tests whether the recovered direction is model-general or dataset-specific.

If this is right

  • If the length-tracking direction is causal, ablating or steering it at inference time could control how long a model's response runs, enabling budget-aware generation without external heuristics.
  • A retraction token that does not produce an upward shift in the probe's estimate could serve as a signature of unfaithful chain-of-thought -- the model says 'wait' but does not internally revise its plan.
  • Prompt-end length estimates exceeding a token budget could trigger early termination before any output is generated, reducing inference cost.
  • The cross-dataset transfer asymmetry suggests that models trained on more heterogeneous data develop more general internal representations of output structure, which could inform training-data curation for controllable generation.
  • If the length signal sharpens with scale, frontier models may carry substantially more precise internal plans for their own output than the 7-8B models tested here, with implications for predictability and steerability of long-form generation.

Load-bearing premise

The 'plan-like' interpretation rests on the cross-dataset transfer asymmetry being genuine and not driven by tokenization differences between natural-language and synthetic datasets; the paper acknowledges that a shared-BPE replication is left to follow-up work and does not empirically rule out this alternative explanation.

What would settle it

Train probes on synthetic and natural-language datasets that share identical tokenizers and BPE boundaries; if the natural-to-synthetic transfer advantage disappears under matched tokenization, the 'plan' interpretation weakens to a tokenizer artifact.

Figures

Figures reproduced from arXiv: 2607.05316 by Adam Oberman, Damiano Fornasiere, Dmitri Carpov, Mirko Bronzi, Mohamed Amine Merzouk.

Figure 1
Figure 1. Figure 1: Predicting remaining tokens on a short example. The answer to “How old is the son?” [PITH_FULL_IMAGE:figures/full_fig_p003_1.png] view at source ↗
Figure 2
Figure 2. Figure 2: Count prediction versus ground truth on a typical example with small MAE. [PITH_FULL_IMAGE:figures/full_fig_p003_2.png] view at source ↗
Figure 3
Figure 3. Figure 3: A high-MAE retraction example, drawn from the worst-MAE region of the eval set [PITH_FULL_IMAGE:figures/full_fig_p003_3.png] view at source ↗
Figure 4
Figure 4. Figure 4: Per-layer probe MAE. MAE-vs-layer for the Remaining Count Probe. Layer 0 = embedding [PITH_FULL_IMAGE:figures/full_fig_p012_4.png] view at source ↗
Figure 5
Figure 5. Figure 5: Per-token-length-bin MAE of the Remaining Count Probe on the eval split, at end of [PITH_FULL_IMAGE:figures/full_fig_p013_5.png] view at source ↗
Figure 6
Figure 6. Figure 6: Retraction example 1. Around completion position 469 the model emits “ [PITH_FULL_IMAGE:figures/full_fig_p017_6.png] view at source ↗
Figure 7
Figure 7. Figure 7: Retraction example 2. Around completion position 608, after the model has written [PITH_FULL_IMAGE:figures/full_fig_p017_7.png] view at source ↗
Figure 8
Figure 8. Figure 8: Retraction example 3. Around completion position 261 the model writes “ [PITH_FULL_IMAGE:figures/full_fig_p018_8.png] view at source ↗
Figure 9
Figure 9. Figure 9: Retraction example 4. Around completion position 500 the model produces a doubled re [PITH_FULL_IMAGE:figures/full_fig_p018_9.png] view at source ↗
read the original abstract

Large language models generate one token at a time, yet their responses show remarkably consistent length structure: step-by-step solutions converge in predictable token counts, retrievals stop after a few sentences, retractions extend responses by measurable amounts. We ask whether the model carries an internal estimate of how much response remains. Training minimal-capacity linear probes on frozen hidden states of three open-weight 7-8B models across seven completion-style datasets, we find three converging pieces of evidence. First, total response length is linearly decodable from the prompt's last hidden state alone, before any output is emitted. Second, probe directions trained on natural-language datasets transfer broadly, including to controlled synthetic completions never seen in training, outperforming a statistical baseline; the converse direction generally fails, and this asymmetry is itself informative. Third, on curated high-loss completions, the probe's per-position estimate shifts upward at the moment the model retracts and restarts a partial solution, a directional behavior no position-only predictor can reproduce (qualitative, not aggregate). We frame this as approximate estimation of remaining generation length, distinct from exact-counting impossibility results for transformers, and interpret it as evidence that LLMs maintain a plan-like internal representation of output length (decodable, not necessarily used causally).

Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, simulated authors' rebuttal, and a circularity audit. Tearing a paper down is the easy half of reading it; the pith above is the substance, this is the friction.

Referee Report

2 major / 6 minor

Summary. The paper investigates whether LLMs maintain an internal, linearly decodable estimate of remaining output length. Using minimal-capacity linear probes on frozen hidden states of three 7-8B instruction-tuned models across seven datasets (two synthetic, five natural-language), the authors report three findings: (1) total response length T is linearly decodable from the prompt's last hidden state alone, beating a constant-median baseline in every cell; (2) probe directions trained on natural-language datasets transfer cross-dataset, including to synthetic targets, while the converse (synthetic to natural) fails—an asymmetry the authors attribute to natural-language training recovering a more general length-tracking direction; (3) on curated high-MAE completions, the probe's per-position estimate shifts upward at retraction tokens, a behavior monotonic baselines cannot reproduce. The paper is methodologically careful in several respects: three-seed averaging, a stratified probe family separating prompt-end decodability from mid-completion updates, and an explicit limitations section acknowledging that decodability does not entail causal use and that the retraction evidence is qualitative.

Significance. The paper addresses a well-motivated question at the intersection of mechanistic interpretability and LLM generation dynamics. Its strengths include a clean probe family design that stratifies contributions (prompt-end vs. mid-completion), a cross-dataset transfer matrix across three model families that goes beyond standard within-distribution probing, and honest scoping of claims (e.g., explicitly framing the retraction result as qualitative, acknowledging the worst-MAE selection bias). The cross-dataset asymmetry result, if it holds up under the controls discussed below, is a genuinely informative finding for the probing literature. The code is released (anonymously), and the hyperparameter and dataset configuration tables (Tables 6-7) support reproducibility. The per-layer sweep (Appendix A.1) and the classification-probe ablation (Appendix A.8) are valuable additions.

major comments (2)
  1. §4.1, Table 1: The paper's foundational claim is that total response length T is linearly decodable from the prompt's last hidden state alone. The only baseline is the constant-median predictor, which uses zero prompt information. No baseline controls for simple prompt features (e.g., prompt token length, question type, structural cues) that could mechanically correlate with completion length. On natural-language datasets, the probe's improvement over the constant-median baseline (e.g., GSM8K: 42.29 vs. 58.66 for Llama) could partially reflect these content correlations rather than an internal length estimate. A simple regression baseline using prompt token count (and perhaps one or two other surface features) as a predictor of T would help distinguish 'the model encodes a length plan' from 'the model encodes prompt features that correlate with length.' This is load-bearing for the paper
  2. §5, Table 3: The cross-dataset transfer asymmetry (natural → synthetic transfers; synthetic → natural fails) is a central result. The paper argues that tokenization differences are 'unparsimonious as the load-bearing explanation' because a tokens-per-character story predicts symmetric failures, but the matrix shows one-way generalization. However, the argument against a tokenization confound is made verbally rather than empirically. The paper itself acknowledges that 'a shared-BPE replication is left to follow-up work.' Given that this asymmetry underpins the 'plan-like representation' interpretation, at minimum the paper should more precisely characterize what tokenization differences exist across the datasets and why the asymmetry argument is robust to them. Alternatively, a control using a fixed tokenizer across datasets would substantially strengthen the claim. Without this, an artif
minor comments (6)
  1. §3.3: The Completion Length Probe is trained with MSE loss but evaluated with MAE. The rationale for this loss/metric mismatch is not stated. A brief note on why MSE was chosen for training while MAE is the headline metric would help.
  2. Table 2: Several cells show the Remaining Count Probe losing to Exact countdown (e.g., Llama/Count: 34.41 vs. 29.80; Llama/MMLU-Pro: 123.56 vs. 123.31). The paper addresses this in the 'Implied claim' paragraph, but marking these cells explicitly (e.g., with a different symbol) would improve clarity.
  3. Figure 3: The table in panel (b) lists token positions 179-191, but the text references t=173 with r_t=814. The relationship between the table range and the referenced position is unclear; better alignment would help.
  4. §A.9: The selection procedure for the four additional retraction examples is described as sorting by per-completion MAE and walking down from the worst. It would help to state how many completions were examined before these four were selected, to give a sense of prevalence.
  5. Table 7: The Count and Countdown datasets have only 301 train and 301 eval samples. This is quite small compared to the natural-language datasets. A note on whether this affects the cross-dataset transfer results (e.g., whether the synthetic→natural failure is partly a sample-size artifact) would be appropriate.
  6. §2: The related work section is well-structured but could briefly mention prior work on length-controlled generation or length prediction in NLP, as these are adjacent to the prompt-end decodability claim.

Simulated Author's Rebuttal

6 responses · 0 unresolved

We thank the referee for a careful and constructive report. Both major comments identify controls that would strengthen the paper's central claims. We address each below and indicate what revisions we will make.

read point-by-point responses

  1. Referee: §4.1, Table 1: No baseline controls for simple prompt features (prompt token length, question type, structural cues) that could mechanically correlate with completion length. A regression baseline using prompt token count would help distinguish 'the model encodes a length plan' from 'the model encodes prompt features that correlate with length.'

    Authors: This is a fair and important point. We agree that the constant-median baseline is the weakest possible control and that a prompt-feature regression baseline is needed to isolate what the probe is reading beyond surface correlations. We will add this baseline in revision. Specifically, we will train a simple linear regression (and optionally a gradient-boosted regressor) mapping a small set of prompt-level surface features — prompt token count, prompt character count, and question type indicator — to T, fit on the train split and evaluated on the eval split, and report its MAE alongside the constant-median and Completion Length Probe in Table 1. This directly tests whether the probe's improvement over the constant baseline is attributable to surface features that are linearly readable from the prompt alone. We expect the probe to outperform this baseline on the synthetic datasets (where T is a deterministic function of the prompt and the probe recovers it almost exactly, e.g., MAE 5.27 on Countdown), but the comparison on natural-language datasets is the empirically open question the referee rightly flags. We note two partial defenses of the current claims that the revision will make explicit: (1) The cross-dataset transfer result (Table 3) is difficult to explain by surface-feature correlations alone — a probe trained on OpenThoughts-1k transfers to Count/Countdown, which have a completely different surface structure, and a probe trained on MMLU-Pro transfers to GSM8K despite different question formats. If the probe were merely reading 'prompt token count' or 'question type,' it should not generalize across these structurally dissimilar datasets. (2) The per-layer sweep (Appendix A.1) shows the signal is absent at layer 0 (the embedding output) and emerges only in later revision: no

  2. Referee: §5, Table 3: The argument against a tokenization confound for the cross-dataset transfer asymmetry is made verbally rather than empirically. The paper should characterize tokenization differences across datasets and explain why the asymmetry argument is robust to them, or provide a fixed-tokenizer control.

    Authors: We agree that the tokenization argument should be supported empirically rather than only verbally. We will add two things in revision. First, a quantitative characterization of tokenization differences across all seven datasets: for each dataset, we will report the distribution of tokens-per-character, BPE merge depth, and vocabulary overlap with the synthetic Count/Countdown sets. This makes the tokenization landscape explicit and lets the reader assess whether the datasets that transfer well to each other are also the ones with similar tokenization profiles. Second, we will strengthen the logical argument with a concrete analysis: if tokenization mismatch were the load-bearing explanation for transfer failure, we would expect the degree of tokenization mismatch between a train-target pair to predict the transfer MAE. We will test this by computing the correlation between a tokenization-similarity metric (e.g., vocabulary overlap or tokens-per-character ratio) and the off-diagonal entries of the transfer matrix. If tokenization is the primary driver, this correlation should be high; if it is not, the correlation should be weak — which is what we expect given the asymmetry (natural→synthetic transfers despite large tokenization differences; synthetic→natural fails despite the same differences). We note that the asymmetry itself is logically inconsistent with a pure tokenization story: the tokenization gap between, say, OpenThoughts-1k and Count is the same in both directions, yet transfer succeeds in one direction and fails in the other. A tokens-per-character confound predicts symmetric failure, not asymmetric. However, we acknowledge that tokenization could interact with the probe-fitting dynamics in ways this simple symmetry argument does not capture — for instance, revision: no

  3. Referee: §5, Table 3: The argument against a tokenization confound for the cross-dataset transfer asymmetry is made verbally rather than empirically. The paper should characterize tokenization differences across datasets and explain why the asymmetry argument is robust to them, or provide a fixed-tokenizer control.

    Authors: We agree that the tokenization argument should be supported empirically rather than only verbally. We will add two things in revision. First, a quantitative characterization of tokenization differences across all seven datasets: for each dataset, we will report the distribution of tokens-per-character, BPE merge depth, and vocabulary overlap with the synthetic Count/Countdown sets. This makes the tokenization landscape explicit and lets the reader assess whether the datasets that transfer well to each other are also the ones with similar tokenization profiles. Second, we will test whether tokenization similarity predicts transfer performance: if tokenization mismatch were the load-bearing explanation, the degree of mismatch between a train-target pair should correlate with the off-diagonal transfer MAE. We will compute this correlation and report it. We note that the asymmetry itself is logically inconsistent with a pure tokenization story: the tokenization gap between, say, OpenThoughts-1k and Count is the same in both directions, yet transfer succeeds in one direction and fails in the other. A tokens-per-character confound predicts symmetric failure, not asymmetric. However, we acknowledge that tokenization could interact with probe-fitting dynamics in ways this simple symmetry argument does not fully capture — for instance, if the synthetic-trained probe overfits to a narrow direction that happens to align with a tokenization artifact, the failure on natural-language targets could be a generalization failure rather than a tokenization mismatch per se. The correlation analysis we propose would help distinguish these. Regarding a fixed-tokenizer control: this would require regenerating all completions with a shared BPE, which is a substantial experimental effort that revision: no

  4. Referee: §5, Table 3: The argument against a tokenization confound for the cross-dataset transfer asymmetry is made verbally rather than empirically. The paper should characterize tokenization differences across datasets and explain why the asymmetry argument is robust to them, or provide a fixed-tokenizer control.

    Authors: We agree that the tokenization argument should be supported empirically rather than only verbally. We will add two analyses in revision. First, a quantitative characterization of tokenization differences across all seven datasets: for each dataset, we will report the distribution of tokens-per-character, vocabulary overlap with the synthetic Count/Countdown sets, and average BPE fragment length. This makes the tokenization landscape explicit. Second, we will test whether tokenization similarity between a train-target pair predicts the off-diagonal transfer MAE. If tokenization mismatch were the load-bearing explanation, this correlation should be high; if it is not, the correlation should be weak. We expect the latter, given the asymmetry: the tokenization gap between OpenThoughts-1k and Count is the same in both directions, yet transfer succeeds in one direction and fails in the other. A pure tokens-per-character confound predicts symmetric failure, not asymmetric. We acknowledge, however, that tokenization could interact with probe-fitting dynamics in subtler ways — for instance, if the synthetic-trained probe overfits to a narrow direction that happens to align with a tokenization artifact, the failure on natural-language targets could reflect poor generalization rather than a direct tokenization mismatch. The correlation analysis would help distinguish these explanations. Regarding a fixed-tokenizer control: this would require regenerating all completions with a shared BPE across three model families, which is a substantial experimental effort. We will scope this for follow-up work but believe the two analyses above, combined with the existing asymmetry argument, substantially narrow the space of tokenization-based explanations. We will revise the manuscript to make revision: no

  5. Referee: §5, Table 3: The argument against a tokenization confound for the cross-dataset transfer asymmetry is made verbally rather than empirically. The paper should characterize tokenization differences across datasets and explain why the asymmetry argument is robust to them, or provide a fixed-tokenizer control.

    Authors: We agree that the tokenization argument should be supported empirically rather than only verbally. We will add two analyses in revision. First, a quantitative characterization of tokenization differences across all seven datasets: for each dataset, we will report the distribution of tokens-per-character, vocabulary overlap with the synthetic Count/Countdown sets, and average BPE fragment length. This makes the tokenization landscape explicit and lets the reader assess whether datasets that transfer well to each other also share similar tokenization profiles. Second, we will test whether tokenization similarity between a train-target pair predicts the off-diagonal transfer MAE: if tokenization mismatch were the load-bearing explanation, this correlation should be high; if it is not, the correlation should be weak. We expect the latter, given the asymmetry — the tokenization gap between OpenThoughts-1k and Count is the same in both directions, yet transfer succeeds one way and fails the other. A pure tokens-per-character confound predicts symmetric failure, not asymmetric. We acknowledge, however, that tokenization could interact with probe-fitting dynamics in subtler ways: for instance, if the synthetic-trained probe overfits to a narrow direction that happens to align with a tokenization artifact, the failure on natural-language targets could reflect poor generalization rather than a direct tokenization mismatch. The correlation analysis would help distinguish these. Regarding a fixed-tokenizer control: this would require regenerating all completions with a shared BPE across three model families, which is a substantial experimental effort. We will scope this for follow-up work but believe the two analyses above, combined with the existing asymmetry argument, meaning revision: no

  6. Referee: §5, Table 3: The argument against a tokenization confound for the cross-dataset transfer asymmetry is made verbally rather than empirically. The paper should characterize tokenization differences across datasets and explain why the asymmetry argument is robust to them, or provide a fixed-tokenizer control.

    Authors: We agree that the tokenization argument should be supported empirically rather than only verbally. We will add two analyses in revision. First, a quantitative characterization of tokenization differences across all seven datasets: for each dataset, we will report the distribution of tokens-per-character, vocabulary overlap with the synthetic Count/Countdown sets, and average BPE fragment length. This makes the tokenization landscape explicit and lets the reader assess whether datasets that transfer well to each other also share similar tokenization profiles. Second, we will test whether tokenization similarity between a train-target pair predicts the off-diagonal transfer MAE: if tokenization mismatch were the load-bearing explanation, this correlation should be high; if it is not, the correlation should be weak. We expect the latter, given the asymmetry — the tokenization gap between OpenThoughts-1k and Count is the same in both directions, yet transfer succeeds one way and fails the other. A pure tokens-per-character confound predicts symmetric failure, not asymmetric. We acknowledge that tokenization could interact with probe-fitting dynamics in subtler ways: for instance, if the synthetic-trained probe overfits to a narrow direction that happens to align with a tokenization artifact, the failure on natural-language targets could reflect poor generalization rather than a direct tokenization mismatch. The correlation analysis would help distinguish these. Regarding a fixed-tokenizer control: this would require regenerating all completions with a shared BPE across three model families, which is a substantial experimental effort. We will scope this for follow-up work but believe the two analyses above, combined with the existing asymmetry argument, meaningfully narrow revision: no

Circularity Check

0 steps flagged

No circularity found: probes trained on external ground-truth labels, evaluated on held-out data, compared against parameter-free baselines.

full rationale

The paper's derivation chain is self-contained and non-circular. (1) The probes are trained on frozen hidden states against external ground-truth labels (r_t = T - t, Eq. 1), not against their own outputs. (2) The constant-median baseline is parameter-free (the train-split median of r_t), and the exact-countdown baseline reuses the prompt-end estimate T̂_0 with a deterministic decrement — neither is a fitted parameter renamed as a prediction. (3) The cross-dataset transfer matrix (Tables 3, 9, 10) evaluates probes on datasets never seen during training, so the transfer claims are not forced by construction. (4) The synthetic Count/Countdown results are explicitly framed as positive controls ('a probe that performs well on Count and Countdown is verifiably reading the relevant information out of the residual stream and not relying on dataset-wide regularities,' §3.7), not as evidence for the plan-like representation claim. (5) No self-citation is load-bearing: the cited works (Alain & Bengio 2018, Belinkov 2021, Lindsey et al. 2025, etc.) are by different author groups and provide methodological context, not the central premise. (6) The retraction-spike observation (§4.3) is qualitative and the paper explicitly flags its limitations, including the absence of a length-matched control — this is a correctness risk, not circularity. The skeptic's concern about prompt-content confounds is a validity threat, but it does not constitute circularity: the probe's target (ground-truth T) is external to the probe, and no prediction reduces to a fitted input by construction.

Axiom & Free-Parameter Ledger

4 free parameters · 4 axioms · 0 invented entities

The paper introduces no new entities (particles, forces, dimensions, etc.). The 'plan-like representation' is an interpretation of the probe results, not a postulated new entity. The free parameters are standard machine learning hyperparameters and the probe weights themselves. The axioms are either standard mathematical facts or domain assumptions that are acknowledged in the paper's Limitations section.

free parameters (4)
  • Probe weights (linear layer) = trained per (model, dataset, layer) combination
    The linear probe f_theta is a fitted parameter. This is standard for probing studies and not a concern; the probe is the measurement instrument, not the phenomenon being measured.
  • Learning rate = 2e-4
    Standard hyperparameter, not tuned to produce specific results.
  • Max steps = 4000
    Standard training hyperparameter.
  • Generation temperature/top-p/top-k = T=0.7, top-p=0.8, top-k=20
    Used for generating completions to extract hidden states. These are standard decoding parameters, not tuned to the probing result.
axioms (4)
  • standard math Linear probes recover information already linearly available in the hidden state, not computation performed by the probe itself.
    Invoked in §3.3 to justify the minimal-capacity probe design. This is a standard assumption in the probing literature (Alain & Bengio 2018).
  • standard math The median is the optimal constant predictor under L1 loss.
    Invoked in §3.4 to justify the constant-median baseline. This is a standard statistical fact.
  • domain assumption Naturally-terminated sequences (those emitting EOS before max-length cutoff) are representative of the model's general generation behavior.
    Invoked in §3.2. The paper acknowledges this as a selection bias in Limitations: results speak to length estimation conditional on successful termination, not to overrun behavior.
  • domain assumption The cross-dataset transfer asymmetry is not explained by tokenization differences.
    Invoked in §5: 'Tokenization differences are also unparsimonious as the load-bearing explanation.' The paper argues this qualitatively but does not empirically test it (shared-BPE replication left to follow-up).

pith-pipeline@v1.1.0-glm · 20077 in / 2999 out tokens · 304165 ms · 2026-07-07T17:43:46.139339+00:00 · methodology

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