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How Much Is an AI Token Worth? Scaling Laws for Wild AI-Generated Web Text

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Abstract

Web text makes up the majority of pretraining data and is increasingly AI-generated. After applying FineWeb quality filtering, we find that 27.5% of tokens from June 2026 web data are labeled as AI-generated by Pangram, rising to 31.1% by August. Unlike synthetic data or model-collapse setups, this *wild* AI text comes from many models, is written for human readers, and arrives unlabeled in pretraining corpora. How does AI text in the wild affect language model pretraining? To answer this question, we pretrain 800 language models (19.9M to 973M parameters), varying the ratio of added AI tokens to human tokens, and fit scaling laws to held-out losses on both human and AI generated text. For data-starved models, adding AI tokens to pretraining data initially lowers loss on human text, but the benefit saturates as more are added and quickly *reverses* into harm. For models trained on high budgets of human text, AI tokens raise loss almost immediately, while the same number of fresh human tokens keeps lowering it. Existing scaling laws such as Chinchilla (Hoffman et al., 2022), which treat AI tokens as no different from human tokens, fail to predict this behavior. We propose a new scaling law with separate benefit and harm terms that allows the value of an AI token (measured in human token equivalents) to change sign while also reducing to Chinchilla in the absence of AI text. When fit on smaller models, our scaling law predicts the effect of AI text on held-out human-text loss for models up to 3.6x larger with 41% lower error than the best existing law over all AI ratios. It implies that training on unfiltered 2026 web text requires 1.3x as much compute as training on its human subset at 20 tokens per parameter, a gap that grows with the human budget. We therefore recommend filtering AI text when the target is human text, repeating human text before expanding the training dataset with AI-generated web text, and reporting validation loss on human and AI text separately, since at a 2026 crawl's AI share, mixed validation sets hide the harm in 95.5% of harmful runs. AI text remains valuable when the target is AI text. We will release WildAI, an 83B-token corpus with AI, topic, and format labels, all 800 models and code.

Primary area:
foundation or frontier models, including LLMs
Keywords:
scaling laws, pretraining, AI detection, data mixing, data filtering

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
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Paper summary

This paper investigates how naturally occurring AI-generated web text affects language model pretraining when mixed with human-written data. Through controlled experiments across model sizes and data mixtures, the authors show that AI-generated and human-written tokens have different effects on validation loss and propose a scaling law to characterize these differences. They find that adding AI-generated text can improve loss on AI-written text while worsening loss on human-written text, an effect that mixed validation sets may obscure. However, these loss differences do not consistently translate into differences in downstream benchmark performance.

Critical strengths

The paper addresses an important and timely problem: how the growing prevalence of AI-generated web content may affect the pretraining of future language models. Studying naturally occurring AI-generated text makes the investigation particularly relevant to practical data collection.

The authors provide a systematic empirical analysis showing that AI-generated and human-written tokens are not interchangeable in their effects on human-text validation loss. The proposed scaling law offers an interesting framework for characterizing pretraining on mixtures of these two data sources.

Critical weaknesses

The implications for model capabilities remain insufficiently established. Lower next-token prediction loss does not necessarily imply stronger capabilities, and higher loss on human-written text does not by itself establish broader capability degradation. Indeed, Appendix G reports similar improvements in CORE scores from adding AI-generated and fresh human-written text, despite their different effects on human-text loss.

One possible explanation is that AI-generated text has a narrower distribution, as suggested by prior work on generative monoculture [1]. Related work also shows that data repetition can affect memorization and generalization [2]. These findings motivate further investigation into whether the observed loss patterns reflect distributional differences, redundancy, or broader changes in model capabilities. More informative capability evaluations, together with a deeper analysis of diversity and redundancy beyond the reported topic and format comparisons, would strengthen the paper’s conclusions.

The robustness of the findings to provenance-labeling errors needs further validation. The paper uses EditLens for initial selection and Pangram for final labeling, and reports a false-positive check on pre-ChatGPT web text. These are useful safeguards, but they do not fully establish labeling reliability on contemporary web content, particularly partially edited or mixed human–AI text.

The authors should report agreement and disagreement between detectors and examine whether the main findings remain stable under alternative detectors, confidence thresholds, or a manually audited subset. Such analyses would help assess whether systematic labeling errors or detector-induced selection biases materially affect the estimated scaling behavior.

References [1] Wu et al. Generative Monoculture in Large Language Models. ICLR 2025. [2] Hernandez et al. Scaling Laws and Interpretability of Learning from Repeated Data. 2022.

Questions for authors

Relationship between validation loss and model capabilities. Appendix G reports similar CORE improvements from adding AI-generated and fresh human-written text, despite their different effects on human-text loss. How should this discrepancy affect the interpretation of “harm” from AI-generated data? Could the authors provide evidence distinguishing broader capability degradation from changes in distributional fit, for example through diversity-sensitive evaluations or comparisons that control for topic, format, and redundancy?

Robustness to provenance labeling. Given that the data construction relies on EditLens for initial selection and Pangram for final labeling, how sensitive are the main findings and fitted scaling laws to detector choice and labeling errors? Could the authors provide an audit of contemporary web samples, including detector disagreements and partially AI-edited text, or repeat key experiments using alternative labels or confidence thresholds?

Independence of the held-out evaluation. Were the 477M and 973M models excluded from both coefficient fitting and functional-form selection? Appendix D.1 and Table 8 compare candidate benefit and penalty terms using errors on these held-out sizes, making their role in model selection unclear. If these results informed the final functional form, could the authors provide an evaluation with a separate model-selection set and a genuinely untouched test set?

2 comments

Thank you for your insightful review, we hope we can address your questions below and will incorporate them into the final version of the paper!

Capabilities and diversity

Capabilities: We read the harm as harm to human-text loss rather than broad capability loss, and will word it that way in the paper: it shows up on specific tasks, not in aggregate CORE. We find that capabilities differ by task, which we will add an analysis of in the final version of the paper. AI text helps most on how-to and explanatory tasks, matching the formats it over-represents, and least on narrative and entity-knowledge tasks. For example, on HellaSwag, AI text (+4.09) improves more than human text (+2.19), but only on the ⅔ of the dataset that are wikihow items (details and table in our reply to RxJ6). Our topic/format experiment in that reply is the controlled comparison you suggest: given the human topic/format mix, AI text still does far worse on human-text loss than fresh human text (C4 +0.32% vs. −1.79% at 135M), and topic and format explain only 8–17% of the gap.

Diversity: AI text is narrower than human text, even within matched topic × format cells: fewer distinct n-grams in all 44 of the largest cells, and lower embedding (Vendi) diversity in 79 of 80. Matching topic and format closes only 10 to 25% of the lexical gap and none of the embedding gap. Single AI documents are as varied as human ones, the narrowness is across documents, the generative monoculture of Wu et al. (2025) showing up in wild web text. We also note that our law fits the loss better than any of the laws for repeating training data (Table 1). We will add discussion of both of these into the paper for reasons why the human and AI models may perform differently.

Robustness to detector

Four independent detectors on 11,000 documents all separate the pools (AUROC 0.94 to 0.98) and find the human pool indistinguishable from 2021 text. Their misses within the AI pool barely overlap (κ ≤ 0.12), so there is no shared systematic error, and Pangram–EditLens agreement is flat across all 23 crawl months. Refitting under the noise rates the detectors imply leaves held-out error and costs essentially unchanged (C4 0.81 vs. 0.83, 1.34× either way). Mixed documents (4.8%) are excluded from both pools; every detector scores them between the two pools, more AI-like as more of their windows are AI. We will note that lightly edited AI text is under-represented and leave its effects to future research.

DetectorHuman pool flagged2021 web text flaggedAUROC, AI vs. human pool
Binoculars0.68%0.80%0.94
Fast-DetectGPT14.3%14.7%0.95
desklib (DeBERTa classifier)41.3%39.2%0.98
Pangram 4.10.12%0.00%0.94

11,000 documents, official thresholds, every detector reading the same 512-token excerpt.

Held-out independence

Thanks for checking this. The 477M and 973M models were excluded from every coefficient fit, but Table 8 does compare candidate forms on them, and we will say so in Appendix D. We will update the appendix to make this clear, and we also reran selection with 268M as a separate model-selection set, as you suggested: we fit all 27 candidates (Table 8's 16 forms plus the 11 benchmarked laws) through 135M, picked the form with the lowest 268M error, refit it through 268M, and scored it once on 477M and 973M. Selection picks our harm term with a unit AI-token value (η = 1), which still beats all 11 benchmarked laws on every human-text target (C4 0.97 vs. 1.41 for Shukor et al.).

We also fit every law on nested subsets of the development models, through 35.8M, 86.2M, 135M and 268M, and scored each fit on the same 477M and 973M models, which enter no fit. Our law has the lowest error of all 12 laws in 15 of these 16 cells, at extrapolations of up to 27×:

Fit throughExtrapolationC4FW22FW26-HPaloma
35.8M13–27×2.83 / 5.383.08 / 5.473.45 / 5.698.74 / 7.94
86.2M5.5–11×1.86 / 3.212.02 / 3.602.47 / 4.587.11 / 7.90
135M3.5–7.2×1.06 / 2.151.12 / 2.381.56 / 3.116.86 / 8.08
268M (Table 1)1.8–3.6×0.83 / 1.410.85 / 1.501.28 / 2.256.77 / 7.80

Paired RMSE ×10⁻³ on the 477M and 973M models, ours / Shukor et al. joint; each row fits every law only on models from 19.9M up to the listed size.

The one exception is Paloma fit through 35.8M, where our law is third. On C4, its lead over Shukor et al. is significant at every cutoff (95% bootstrap intervals over control groups exclude zero). We will add both protocols next to Table 1 in the final version.

As the discussion period nears its end, we wanted to check in and see if our response has addressed your concerns, particularly about including more discussion of model capabilities. Please let us know there is anything else we can clarify further and we would appreciate it if you would consider updating your assessment if your concerns have been resolved. Thank you!

Reviewer_RxJ6OpenReview ↗
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Paper summary

The paper uses Pangram to show that AI-generated text on the web is constantly growing and has risen by about 20% on FineWeb filtered web tokens in the past 2 years. The authors train several model sizes on AI text added to human text and measure performance as they vary the amount of AI text. They then identify the regimes where the AI text helps and also show when it harms. Accordingly, they fit scaling laws with separate benefit and harm terms, and recommend filtering AI text and repeating human text.

Critical strengths

The paper's main strength is that it addresses an interesting problem which is that AI text is increasing heavily all over the internet. LLMs are pretrained on webfiltered data and previous scaling laws treated this data equally, since some years ago it was mostly human text. Nowadays, the web is full of AI text and it's interesting to see how this affects the scaling laws and the performance of the models trained on current web filtered data.

Critical weaknesses

The main weakness of the paper is the main evaluation setup used which makes the paper of less practical significance. To be specific, the idea of benefit then harm only applies to the human text used for evaluation and not to the benchmarks, which makes the findings less interesting. The harm part, which suggests filtering AI text, is only relevant if we are optimizing for human text prediction, but was not shown to matter and does not harm for other tasks or benchmarks. So looking at the big picture, when curating datasets for pretraining, is the AI text on the web really worth filtering? The results on CORE suggest that an AI token is worth roughly a human token.

Another concern in the evaluation setup is the categorical composition of the AI and human text. If the human and AI text used for training have very different topics/content/distribution (Figure 2), then the AI harm could be arising simply from content mismatch rather than being AI generated.

Questions for authors
  • Did the authors consider using another AI detector beyond Pangram like GPT-Zero for example? If feasible, it would be interesting to the see if the same scaling laws hold using another detector.
  • What is the motivation behind using FineWeb filtering? Would also be interesting to the see the effect on other filtering styles like DCLM, since LLMs pretrained on DCLM usually have stronger benchmarks results than FineWeb.
7 comments

Thank you for the insightful review! We hope to address your questions below and will incorporate the new results into the final version of the paper.

Is harm arising from content mismatch rather than AI-generation? (W2)

We also wondered this, and decided to keep the mismatch on purpose, since this reflects what wild AI text is: AI text leans toward tutorials, knowledge articles and listicles (Figure 2), and the web as a whole is shifting toward the formats AI writes most (Figure 8). However, we agree it could be an important confound, so we ran a 2×2 matrix, AI or fresh human text, each with its own topic/format mix or the other pool's mix. We find matching barely changes results, as AI text still raises C4 and FW22 loss while fresh human text lowers loss on every target. Topic and format account for only 8%-17% (the loss change from swapping the topic/format mix), and authorship for the rest.

Added text (r = 1)C4FW22FW26-H
AI text, AI mix (as in the paper)+0.64 / +0.47 / +0.57+0.50 / +0.37 / +0.47+0.31 / +0.24 / +0.36
AI text, human mix+0.43 / +0.32 / +0.32+0.26 / +0.18 / +0.19−0.05 / −0.06 / −0.02
Fresh human text, human mix (as in the paper)−1.74 / −1.85 / −1.79−1.84 / −1.97 / −1.94−1.95 / −2.16 / −2.13
Fresh human text, AI mix−1.59 / −1.61 / −1.56−1.63 / −1.71 / −1.67−1.59 / −1.70 / −1.67

Change in loss vs. the human-only control (%), 35.8M / 86.2M / 135M.

Is AI text really worth filtering?

We definitely think so! Filtering matters for human-text loss and for some capabilities. Overall CORE moves about the same with AI and fresh human text, but individual tasks show discrepancies.

AI text helps most on how-to and explanatory tasks, matching the formats it over-represents, and least on narrative and entity-knowledge tasks. For example, on HellaSwag, AI text (+4.09) improves more than human text (+2.19), but two-thirds of its examples are WikiHow how-to items. On these, AI text gains +5.22 against +2.35 for human text (AI − human +2.87, 95% CI 2.39 to 3.39), whereas on the remaining ActivityNet examples there is no AI advantage (+1.73 vs. +1.87; −0.14, CI −0.39 to +0.12). We'll add the per-task analysis to Appendix G to better explain the differences in capabilities between the heavily AI and heavily human models.

Our topic/format experiment show why. HellaSwag's gain comes from format. Fresh human text given AI text's topic/format mix gains as much as AI text (0-shot +5.46 vs. +5.17). LAMBADA's deficit comes from authorship. Given the human mix, AI text still trails fresh human text (+0.15 vs. +1.78). So the HellaSwag advantage is available from human text in the same formats, while the LAMBADA cost comes with AI authorship itself. We’ll add this as discussion on these topics and suggest future research study the intersection of topic/format/and ai authorship filtering.

TaskFresh human textAI textAI minus human [95% CI]
LAMBADA+3.74+0.45−3.29 [−3.72, −2.88]
BIG-bench QA Wikidata+5.76+1.65−4.11 [−5.20, −3.11]
COPA+3.76−2.16−5.92 [−8.96, −2.72]
HellaSwag (0-shot)+2.19+4.09+1.90 [1.57, 2.24]
PIQA+2.95+4.64+1.68 [0.99, 2.32]
SQuAD+2.07+4.15+2.08 [0.98, 3.42]
CORE+1.82+1.76−0.06 [−0.51, 0.41]

Change in centered accuracy points vs. each run's own control, over 25 matched pairs with r ≥ 1.

Did the authors consider a different AI detector?

Top AI-detection services are expensive on large corpora, so it was beyond our financial resources to use GPTZero as well. Our pools were labeled by two detectors, EditLens and then Pangram, which agree on 98.6% of documents (excluding Mixed), and Pangram labels only 0.06% of 60,000 pre-ChatGPT documents as AI (Appendix A). To better address this concern, we ran four other detectors (Binoculars, Fast-DetectGPT, desklib and Pangram 4.1) on 11,000 documents. All of them separate the pools (AUROC 0.94 to 0.98), and refitting the law under the label noise they imply leaves held-out error and costs essentially unchanged (details in our reply to DFQD).

Why FineWeb filtering rather than DCLM?

Initially, we decided to use Fineweb because the released Fineweb corpus extended through mid-2025, compared to DCLM which went through 2023, and 2025 would give us much more AI generated data. We did find that DCLM keeps AI documents 9.8× as often as human ones, vs. 2.3× for FineWeb, so DCLM-filtered data would contain even more AI text and we estimate our findings would matter even more using that filtering schema.

Thank you for the response and additional experiments.

My main concern is still not fully addressed. The harm from AI text and the recommendation to filter it are based on the loss on human text. A model trained on more human text will naturally predict human text better, so this is expected given the evaluation setup. For pretraining data curation, what matters more is the model's capability and human text prediction is not a good proxy for this here. For capability, the new experiments show that AI and human text contribute similarly (CORE difference −0.06, CI −0.51 to 0.41).

  1. Why should loss on human text signal filtering AI text in pretraining data? The benefit then harm pattern does not appear in the benchmarks and AI text improves almost every task.

  2. The 2x2 results suggest that the harm depends on which human text is used for evaluation, where matching the topic mix can remove the harm as on FW26-H. This seems to be a mismatch between added text and evaluation text rather than an indicator to filter AI text.

  3. If we used AI text for evaluation instead, wouldn't that reverse the results and hint at requiring more AI text and filtering human text?

Thank you for engaging with the rebuttal!

Clarification: the harm is not relative to a model trained on more human text.

Each AI run keeps all of its control's human tokens and adds AI tokens on top, so each model is compared against a control trained on exactly the same human data, with nothing added. Extra data from a related distribution usually helps, so we find it non-obvious that adding AI web text would hurt held-out loss (once models are trained on more than ~20 TPP_h). Specifically, we find at 5 TPP_h, none of the 83 runs with ≥25% AI raises loss on C4, FW22 or FW26-H. At 40–100 TPP_h, all 153 do.

Q1. Why should human-text loss signal filtering?

Because benchmark accuracy and fit to human text are different goals, and aggregate CORE is too noisy at our sizes to separate AI from human text. At 20 TPP_h, adding at least as many tokens as the human corpus holds raises CORE similarly (+1.6 points with AI text, +1.9 with fresh human text), while C4 loss moves in opposite directions (+2.3% vs. −3.0%; Appendix G).

Benchmarks that depend on predicting human text do show the turn, most clearly LAMBADA. The gain from added AI text per doubling of data falls from +1.39 points at 5 TPP_h to −0.10 at 20 and −1.10 at 40+, while fresh human text keeps helping (+2.92, +1.37, +1.19). BIG-bench QA Wikidata and COPA trend the same way. Models can also match on CORE while differing on less verifiable qualities CORE doesn't measure, such as writing style or vibe. For example, models trained with AI text use roughly twice as many AI-typical phrases as human-only models (Figure 24). Several CORE tasks are still near chance at 1B parameters or smaller, which is part of why we focus on held-out loss. We will add per-task CORE results to the final version to expand on what tasks AI helps vs where human helps.

Q2. Is the harm a mismatch between the added and the evaluation text?

Only a small part of it. We trained the grid of text source × topic/format mix (135M, r = 1). Change in FW26-H loss vs. the control:

AI topic/format mixHuman topic/format mix
AI text+0.36%−0.02%
Fresh human text−1.67%−2.13%

Matching the human mix removes the harm relative to the control, but not the gap between an AI and a human token. In models with the same mix, human text lowers loss by 2.13% while AI text leaves it flat.

To adress this concern more fully, we have trained 104 proxy models (19.9M) in the style of RegMix [1], varying the AI share, topic mix and format mix independently. At fixed composition, each 10 points of AI share raises FW26-H loss by 0.61% (C4: 0.65%), and AI share alone predicts loss on held-out mixtures just as well as the full model with topic and format.

In practice, the mix of topics and formats is not freely known. The topic and format labels are a contribution of our dataset, as we label our 83B tokens with both WebOrganizer classifiers, taking about 80 H100-hours (roughly 15,000 for a 15T-token corpus). Matching AI text's mix to human text's is itself a filter (it would cut AI-written knowledge articles and tutorials about threefold), and the web is moving toward the formats AI writes most (Figure 8). We also agree with you that there is no single correct evaluation distribution: we evaluate on C4, FW22, FW26, Paloma and Cosmopedia, and each has its own mix of topics, formats, and AI use. So even where the mix explains part of the harm, the solution would still be to limit AI text (by reducing overly represented topics/formats from AI).

Q3. Wouldn't evaluating on AI text reverse the results?

No, because the effect is asymmetric. We evaluate on two AI-generated sets, FW26-AI (held-out 2026 AI documents) and Cosmopedia. AI text lowers FW26-AI loss a lot, but fresh human text lowers it too, albeit less so (−17% vs. −3% at 135M, r = 1). In the other direction, AI text raises loss on held-out human text once models pass ~20 TPP_h, while human text lowers it. Human text helps on both, whereas AI text helps only on AI text.

In the final version we will add the per-task CORE results, the topic x format mix experiment, the RegMix experiments, and a clearer description of the additive setup. We hope this clarifies why we use loss on held-out human text as our main evaluation!

[1] Liu et al., "RegMix: Data Mixture as Regression for Language Model Pre-training," ICLR 2025.

Reviewer_E7oTOpenReview ↗
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Paper summary

This work presents empirical evaluations on the effect of real-world AI-generated data on LLM pretraining. First, it measures the amount of AI text in web crawls over time and across different topics and formats, as well as its survival through FineWeb and DCLM quality filters. Then, the authors pretrain 800 models in the range 20M-973M parameters with varying ratios of AI text to fit scaling laws to test loss. The experiments show that AI text can be helpful for data-starved models, and that benefit saturates and reverses for sufficiently large AI text ratios. The authors then proposed a modification to the Chinchilla scaling law, motivating recommendations to filter AI text, repeat human text before adding AI text, and report separate validation losses on human and AI text separately.

Critical strengths
  1. The problem of the paper is timely, as AI-generated text makes up a growing share of web crawls, so it will inevitably contaminate future training data.

  2. The paper shows that the provenance of a document affects its utility independently of quality as defined by standard filters.

  3. The experimental design is clean and thorough within the claimed scope. Training 800 models with control runs that train on matched human datasets allows for proper comparison.

  4. The results give insight into practical adjustments for LLM pretraining, e.g. that a mixed (AI+human data) validation set hides 95.5% of harmful runs.

Critical weaknesses
  1. The relevance of Dohmatob et al. (2024; 2025) is understated. These prior works study how the presence of synthetic data changes the scaling laws through a theoretical model for LLMs. Their predictions also match this work's results, namely that at a fixed synthetic ratio more data eventually stops helping LLM training, reaching a plateau. The fitted law in this work has v>0v>0 and loss eventually rising with DHD_H for fixed ratio rr. The paper should benchmark an adapted form or discuss where theory and results (dis-)agree.

  2. The “AI text” target behind the >90% optimal share, the >20-human-token first AI token, and Fig. 19 is Cosmopedia, a curated, single-model (Mixtral), early-2024 synthetic corpus of textbooks and stories, i.e. the kind of data the paper itself distinguishes wild AI text from, while the wild target FW26-AI is 3.5M detector-labeled tokens.

Questions for authors
  1. Newer models show fewer hallucinations and provide greater capabilities. Your results in Appendix G already suggest that current AI-generated text helps with increasing CORE scores. Yet your forecasts assume that the value per token stays fixed as time goes on. Can you test whether the utility of a synthetic document is correlated with its timestamp?

  2. Can you discuss in more detail whether there are any divergences between your findings and the theoretical findings of Dohmatob et al. (2024; 2025)?

  3. Could the headline AI-target results be reported on FW26-AI as well?

3 comments

Thanks for the thoughtful review and the great questions. We will add the new results to the final version of the paper!

Relevance of Dohmatob et al. (2024; 2025) is understated

These papers did shape a lot of the research questions we asked, so we will make sure to emphasize their importance in the final version of the paper. For both papers, we’ve added adapted versions of the theoretical models into scaling laws. We find that neither model performs better than Chinchilla or our proposed methods when evaluating on human text for the held out sized models. will add these results to table 1, as well as a description of each scaling law in the appendix.

LawC4FW22FW26-H
Strong Model Collapse (adapted)7.907.907.82
A Tale of Tails (adapted)4.384.745.54
Chinchilla4.324.655.40
Ours0.830.851.28

Held-out paired RMSE ×10⁻³ on the 477M and 973M models, as in Table 1.

Dohmatob et al. and our results agree that more human data helps less as the ratio of AI data increases, but differ at low budgets: in our runs AI text helps data-starved models and turns harmful from about 10–20 TPP_h, a sign change neither adapted law can produce (Strong Model Collapse has a constant floor, and A Tale of Tails has no harm term).

You bring up a good point about the eventual rise of harm. Our law’s eventual rise sits beyond budgets of AI that we trained for, but it would be a good extension of this work to train more models at large budgets to confirm if there will be a plateau or rise. We agree either could be very plausible. We fit a version of our law that does plateau (harm of Eq. 4 added to the loss and capped beyond a fitted budget ts by the factor 1/(1+(t/ts)u)), and find it has a held-out error of 1.05, compared to 0.83 for our proposed law.

We note that a continued rise is also plausible. Dohmatob et al. (2025) show that larger models can amplify collapse, and Hernandez et al. (2022) show that a small amount of repeated data can degrade an 800M model to 400M-level performance. We will add discussion of the potential rise or plateau as a still open question to the paper, mentioning that both rise and plateau laws performed well.

Highlight FW26-AI instead of Cosmopedia

This is a good point. We chose to highlight Cosmopedia because it is a widely used, public synthetic corpus (Ben Allal et al., 2024). We will add FW26-AI to visuals for the final paper. Below, we report that the headline results hold on FW26-AI, slightly more strongly.

Headline (268M)Cosmopedia (paper)FW26-AI
Loss-minimizing AI share, 5 to 100 TPP_h93.4 to 98.5%94.0 to 98.5%
Value of the first AI token, in human tokens22.525.5
Largest loss reduction from AI text at 5 / 20 / 40 TPP_h (Fig. 19)25.2 / 17.9 / 14.0%29.8 / 22.5 / 17.5%
AI runs that lower loss on the target553 of 553553 of 553

How does the utility of AI data change over time?

We made and trained some small models, one on early 2024 text and another on late 2025/2026 text. Newer AI text does less harm (30–40% less on C4 and FW22 at r = 1), though at r = 1 it still raises human-text loss. We will add discussion of this to the paper, that as models change, we cannot assume the utility of the AI generated text will remain the same as it is today. We will include discussion of this as a future line of work.

Model, rC4FW22FW26-AI
19.9M, r = 0.25+0.06 / −0.12−0.00 / −0.16−7.18 / −9.14
19.9M, r = 1+0.69 / +0.46+0.60 / +0.36−11.00 / −14.16
35.8M, r = 0.25−0.01 / −0.04−0.08 / −0.11−7.89 / −10.46
35.8M, r = 1+0.81 / +0.57+0.73 / +0.47−11.94 / −16.51
86.2M, r = 0.25+0.01 / −0.06−0.02 / −0.08−8.51 / −12.59

Change in loss vs. the human-only control (%), early-2024 AI text / 2025–26 AI text. Lower is better.

As the discussion period nears its end, we wanted to check in and see if our response has addressed your concerns, particularly regarding the comparison to the Dohmatob model collapse papers. Please let us know there is anything else we can clarify further and we would appreciate it if you would consider updating your assessment if your concerns have been resolved. Thank you!

I would like to thank the Authors for addressing my points. I am satisfied with the rebuttal, and will thus maintain my positive score.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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