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Under review as a conference paper at ICLR 2027

A Dominant Supplier Slows Recursive Drift More Than It Steers It

Abstract

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.

Primary area:
foundation or frontier models, including LLMs
Keywords:
model collapse, recursive training, synthetic data, multi-model ecosystems, data concentration, self-consuming loops, language models, homogenization

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_jsfkOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

The authors analyze how LLM outputs drift when they are finetuned on a shared corpus of each other's text. In their experiments, the models start outputting fewer "function words" (the most frequent words in English) and do not repeat themselves. Furthermore, the authors report that increasing Phi-2's share of the corpus does not necessarily "align" the other models' outputs closer to Phi-2's. For more concrete analysis, they introduce definitions of "delay" and "departure" from a reference drift trajectory, and use these tools to analyze drift while varying how much of the corpus each model contributes. Their conclusions also vary based on the share percentage and the dominant model.

Critical strengths

The authors address an interesting and timely problem, related to model drift and collapse due to finetuning on the mixed outputs of other models. The authors use diverse metrics like drift, separation, delay, departure to analyze how each model's outputs change.

Critical weaknesses

I did not see justification for why the authors' results shed insight on the real-world problem they're motivated by. Some reasons why this is not obvious: (a) the models are relatively small (1B-3B) base models, not instruction-tuned, and the corpus consists of short (<=128 token) continuations; (b) each generation resets to base weights, and the authors never experiment with a continual learning setup; (c) sampling involves non-standard frequency and repetition penalties. I don't think the authors' experiments have to replicate real-world settings to shed insight on their real-world problem, but I need justification/convincing why insight transfers.

Questions for authors
  1. Please improve the writing in Section 3: Setup, I found the paper hard to read. In particular, the setup is a large number of definitions and metrics with little justification/intuition for where they come from, and many of the specifics can be moved to the appendix. Also, terms like "departure" and "delay" appear in the abstract/main text before they are defined.
  2. The authors chose DeBERTa as their sequence encoder because it "separates arms more sharply from seed noise", i.e. based on the same results it is being used to report. Results would be improved by varying the sequence encoder. As it stands, two issues: (a) greater separation does not mean the results are more valid. For example, greater separation may simply be due to difference in surface-level features like function-word rate (which is somewhat artificially lowered by the authors' frequency and repetition penalties); (b) The authors' key result about steering towards Phi-2 seemingly only holds under DeBERTa and not under e.g. all-mpnet-base-v2. Varying the sequence encoder lets us extract more generalizable insight.
  3. In the experiments, the authors only used two seeds per arm and a seed floor estimated from two runs. The between-seed variation in results (e.g., in Table 1) can be quite large, so ideally the results have confidence intervals and more seeds.
  4. Many of the claims sound like over-simplifications. For example, the authors claim the 90% arm ends at an earlier stage of the uniform arm. But across metrics: the 90% arm matches the uniform arm's generation ~3 on perplexity, ~4 on function-word rate, ~5 on word length, etc. Can we make the claims more precise?
Reviewer_rY6qOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies recursive fine-tuning of eight base models on a shared pool of their outputs, varying the share produced by one model. Each generation restarts from the pretrained weights and trains on 2,100 texts. The authors separate embedding drift into changes in direction and pace, and find that giving Phi-2 90% of the pool mainly slows the drift.

Critical strengths
  • The experimental procedure and measurements are clearly explained.
  • The authors include alternative dominant models, human-text mixtures, and a decoding ablation.
Critical weaknesses
  • The setup is quite contrived. Given a fixed compute budget, there is no clear reason to spend it on this recursive process instead of directly training a model on an appropriate corpus. The authors motivate this through model-generated text entering future web crawls, but do not establish that their setup meaningfully represents this process. Every model repeatedly restarts from its original base weights and is fine-tuned on a small shared pool of generated texts. It is unclear why this would be representative of how actual language models are trained. The existence of earlier studies using similar loops does not resolve the weak practical motivation.

  • Even accepting the setup, the contribution is fundamentally incremental. Vu et al. (2025) already study models recursively training on each other's outputs, and Hodel and West (2025) study the effects of concentration across models. The additional observations about supplier shares and drift speed provide limited new understanding. This is exacerbated by the quite weak experimental scale. The main analysis centers on Phi-2, a small 2.7B model, and all eight models have only 1B to 3B parameters. Each generation involves one epoch of fine-tuning on 2,100 short texts. There is no indication whether the findings scale to larger models, larger corpora, or more substantial training. These experiments are insufficient to support conclusions about dominant suppliers in a realistic model ecosystem.

This is a fundamentally incremental study with weak practical motivation and quite limited experimental scale. Even accepting the recursive training setup, the paper adds little understanding beyond the existing literature. I therefore recommend rejection.

Questions for authors

I understood the authors' intent and the manuscript. I do not have specific questions that need to be addressed.

Reviewer_wxwNOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

The authors examine a setting where a single LLM authors most of the text that a group of models is trained on, in order to determine whether the dominant LLM pulls the others toward its own writing, or changes how fast they drift away from their initial state. They simulate the loop with eight small open-weight models - in each generation every model writes continuations of human-authored prompts, the texts are pooled according to predetermined proportions, and every model is fine-tuned on the pool from its base weights over multiple iterations. The pool share written by one model, Phi-2, is varied from an equal split to 90%, two other models are given half the pool in turn, and human text fills part of the pool in two further runs. Changes in each model's output are tracked with a frozen text encoder. All models turn out to change in the same way, so the authors separate the effect induced by the most dominant model in the pool into two parts: Whether it delays the drift of other models along that common path, and whether it pushes them away from it.

Following the analysis of their experimental findings, the authors draw the following conclusions: 1) All models drift together toward a style with fewer function words, and none collapses into repetition, 2) No share of Phi-2 brings the other models closer to its text than the equal split does, 3) Most of the gap is delay, 4) Which model dominates decides whether the group slows at all, 5) Human text delays the models along the same path.

Critical strengths
  • The research question is new and timely, and the experimental design is methodologically sound, tracking a wide range of relevant phenomena. Every comparison between the evaluated configurations uses the same prompts and random seeds, and each difference is judged against how much two runs of the same configuration differ by chance (i.e. establishing a noise floor). The authors furthermore check their findings with a second encoder and with two simple text statistics that do not depend on any encoder, giving a level of generalizability to their findings. They also designate multiple models as dominant within the examined pools, which shows whether the observed effects are independent from the identity of the dominant model.
Critical weaknesses
  • The presented findings are primarily the consequence of a specific experimental setting, rather than of recursive training on web text which the paper aims to explore. Every model restarts from its base weights for each generation and is fine-tuned once on ~2k short texts, so any influence of the dominant model is erased before it can build up. The paper finds no pull toward the dominant model and explains in the discussion that such a pull would need signal accumulation, which arguably would be present in a web-scale setting that the introduction describes (since LLM-authored data is expected to accumulate in web-based resources over time). Additionally, the drift that all models follow is attributable to the sampler's repetition and frequency penalties, which the paper states only in its conclusion, and the spread and steering results change under the second encoder, which is also the one that prior art uses. To make the contribution stronger, the authors are encouraged to add a configuration that continues from the previous generation's weights, conduct and report a full ablation study with the alternative sampler, justify the encoder choice, and either explain how the simulation maps onto web-scale training or drop that framing.

  • The results section is hard to parse, due to being very dense and restating numerical findings already documented in tables, rather than focusing on synthesizing and analyzing said results. More significantly, the conclusion discloses that the drift all models follow, i.e. the loss of function words, comes from the sampler's repetition and frequency penalties. This finding reframes how every result reported up to that point should be interpreted - the paper actually measures how the dominant LLM impacts the spread of a sampling artifact, and not a general property of recursive training. This information belongs in the setup section, and the results sections should be rewritten with that framing firmly established.

Questions for authors
  • The primary encoder (DeBERTa) was chosen because it separates configurations from seed noise more sharply than the sentence encoder used in prior work (all-mpnet-base-v2). However, there is a risk that a method chosen in this manner may be measuring something other than the style change of interest. Two of the reported findings - the spread of the group and the pull toward Phi-2 - change under the second encoder, which points towards this concern being a reasonable one. What does the DeBERTa encoder capture that the sentence encoder does not, and why should the reader trust its readings where the two disagree?

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

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