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Under review as a conference paper at ICLR 2027

The Lottery Circuit Hypothesis: Sparse Mechanisms from Randomness

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Abstract

Interpretable AI, and mechanistic interpretability in particular, aims to uncover the internal computations of language models, with circuit discovery remaining an important approach. We propose the Lottery Circuit Hypothesis: sparse, task-functional circuits can be constructed by zero-based masking of random-weight transformers, rather than merely extracted from computations established through pretraining. This reveals a possibility in circuit discovery that bears on what we call the provenance assumption: that a sparse subgraph reproducing a target task behaviour thereby localises computation already encoded in the pretrained weights. Motivated by the strong lottery ticket hypothesis, we perform circuit discovery beyond pretrained models and find that DiscoGP can construct sparse, high-performing weight-and-edge circuits in randomised transformers. We further demonstrate concealment: task-agnostic, small-magnitude fills obscure the trace of zero-based weight pruning while preserving task performance. This extends the perturbation perspective of neural thickets from neighbourhoods of pretrained models to neighbourhoods of masking-constructed subnetworks within random models. We give a theoretical account of what we call margin synthesis by linking this constructive capacity to mask granularity: in a simplified additive model, each edge contributes a sum of independent, zero-mean Gaussian terms, normalised by , to the task margin. Weight pruning can retain favourable terms within an aggregate and attain , whereas edge pruning selects among aggregates of magnitude . Together, these results call for a rethinking of circuit discovery: a discovered circuit may be a mask-induced construction, and interpreting it as a map of pretrained computation requires additional treatment and evidence.

Primary area:
interpretability and explainable AI
Keywords:
mechanistic interpretability, circuit discovery, sparse subnetworks, lottery ticket hypothesis, explainable AI

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_BqrJOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
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Paper summary

This paper investigates what the authors call the lottery circuit hypothesis. The authors demonstrate experimental results showing that task-functional circuits can emerge from zero-masking-based circuit discovery performed on random-weight transformers. The paper also shows that we can hide the trace of exact-zero-masking by refilling the zero-masked weights with newly generated random weights that approximate a Gaussian distribution together with the unmasked weights. A minimal toy theoretical modelling is provided to rigorize the results.

Critical strengths

(1) The paper performed extensive experiments to clarify and support their claims and results.

(2) Distributional refill after masking-based circuit discovery can retain useful behavior is, to some extent, an interesting observation.

Critical weaknesses

(1) The biggest deal-breaker for me is that the extensive analysis of the problem the authors study seems without a motivation that is compelling or justifiable. Lottery circuit hypothesis is not surprising given strong lottery ticket hypothesis, and task-functional circuits might be a result of the circuit discovery method itself is not news: there has already been works performing circuit discovery on random transformers. (See my questions) Distributional refilling, while an interesting insight, offers little practical value for circuit discovery researchers. Its setup is a narrow contrivance.

(2) The writing of this paper needs great improvement, with a lot of technical details missing and explanations of the experimental results often scattered far away from the results themselves. The use of terminologies that are not defined also causes a lot of confusion.

Questions for authors

At this point, I am inclined to reject this work, unless the authors resovle my doubts about their paper's motivation.

(1) The take-home message from the lottery circuit hypothesis is that the task-functional circuit could be a result of the circuit-discovery method being able to "learn" the task. There has already been at least one previous work [1] on this, which also performs circuit discovery on random-weight transformers. I wonder how your work furthers or differs from their insight.

(2) I do not see the practical value of distributional refilling. How do you expect this insight to change or guide future practices of circuit discovery or interpretability research in general?

(3) What is the fundamental difference between your lottery circuit hypothesis and strong lottery ticket hypothesis and supermasks? Both show how masking can learn for a specific task, right?

(4) A lot of contents are discursive and off-topic: Table 1 is a discussion on DiscoGP's property. Table 2 also feels uninformative. Why do we want to compare the circuit density of pretrained and randomised transformers? Figure 3 and 4 are properties of distributional refilling, which is not useful unless the previous question regarding the latter's motivation is properly addressed. Figure 5 fixes a problem on randomised transformer circuit discovery. I wonder how this can be useful. We almost never perform circuit discovery on randomised transformer, and there are a lot of other ways of randomisation.

Other minor suggestions/questions:

(5) You should define or clarify the following things:

  • "task margin" on line 84.
  • λθ\lambda_\theta and λE\lambda_E on line 94-95. Moreover, the loss where these regularization coefficients show up is never defined.
  • "refilling" and "completion" are used exchangeably, which is confusing.
  • "selection"on line 265 appears abruptly.

(6) The transition between the two paragraphs on lines 201-215 needs to be clarified. They are different refilling schemes.

(7) The paragraph on line 210 requires major rewriting: it is the key technical detail of distributional refilling, but much of it is conveyed in rather abstruse language. The two-components reference distribution and the Gaussian bin-filling both warrants detailed discussion.

(8) A few other citations might be added for "variation among circuits" in the related work [2-4].

(9) Much of the circuit behavior is quantified using “accuracy” (Equation 3), defined as the fraction of examples with a positive task margin. This thresholded metric discards the magnitude of the margin and may therefore obscure behavioral differences between circuits. Would examining logit diff or prob diff, as discussed in [5], provide a more fine-grained characterization? Could the authors contextualize their choice of accuracy, including references to prior circuit-discovery work using this metric? This is not a major concern for my assessment. I just want a clarification.

I will consider improve my rating if the authors adequately address the above questions.

[1] Méloux et al. (2025). The Dead Salmons of AI Interpretability. arXiv:2512.18792.

[2] Rai et al. (2026). Data-driven Circuit Discovery for Interpretability of Language Models. arXiv:2605.09129.

[3] Wu et al. (2026). Demystifying Variance in Circuit Discovery of LLMs. arXiv:2606.16920.

[4] Cho et al. (2026). Shared Semantics, Divergent Mechanisms: Unsupervised Feature Discovery by Aligning Semantics and Mechanisms. ICML.

[5] Hanna et al. (2026). Have Faith in Faithfulness: Going Beyond Circuit Overlap When Finding Model Mechanisms. COLM.

Reviewer_5cZqOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

The paper asks whether a circuit found by a circuit-discovery method can be read as evidence that the computation was learned in pretraining. The authors call this the "provenance assumption". To test it, they randomise the attention and MLP weights of GPT-2 Small/Medium, Pythia-410M and Qwen2.5-0.5B while embeddings, unembeddings and norms stay pretrained. They then run DiscoGP, which learns binary masks over individual weights and over graph edges, on three binary token-choice tasks (IOI, BLiMP, Docstring).

The dense random models are at chance, but the masked circuits reach accuracy comparable to circuits found on pretrained weights, with very few edges (Table 1, Table 3). The authors call this the Lottery Circuit Hypothesis. They then refill the zeroed weights with small, task-agnostic, Gaussian-shaped values. The circuit largely survives (Table 3, Fig. 3, Fig. 4), and a new edge-only search on the completed weights finds circuits again (Table 4). The authors conclude that a discovered circuit may be a mask-induced construction, and that reading it as a map of pretrained computation needs further evidence.

While the point made by the paper that existence of circuits in models is not necessarily a consequence of the pretrained weights, this finding is not entirely novel given the existence of the Strong Lottery Ticket Hypothesis. Additionally, the writing and exposition of the paper make it very difficult to follow.

Critical strengths
  • The question regarding weight discovery is worth asking. Circuit discovery has no standard random-weight sanity check for saliency maps. The paper makes the case for one.
  • The experimental setup has reasonable breadth: four models, three tasks, and ten random initializations for the construction results (Table 3).
Critical weaknesses
  1. Limited novelty relative to strong lottery tickets.

    • The paper frames itself as an application of the strong lottery ticket (SLT) idea: masking frozen random weights yields a working subnetwork.
    • Given SLT results and the cited work on random transformers, the main finding is an expected one. A mask with enough degrees of freedom, trained on a narrow task, will fit that task.
    • The paper never says what is surprising relative to SLT. The same "random weights solve the task" result on a binary token comparison was foreseeable.
  2. The claim is much broader than the evidence.

    • The abstract and conclusion talk about circuit discovery in general. The evidence covers one method, DiscoGP, and mainly its weight-level masks.
    • The paper's own Table 1 shows that edge-only discovery largely fails on random weights, while it works on pretrained weights. Edge-level methods (ACDC, EAP, Edge Pruning) are what most of the field uses.
    • The data suggests pretrained weights do matter for those methods. That is against the claim that the "success doesn't imply pretraining" message by the authors.
  3. The pretrained aspect is not tested.

    • There is no comparison between pretrained-weight and random-weight circuits. Overlap, structure, out-of-distribution behaviour and robustness are all unexamined.
  4. The writing is very hard to follow.

    • The research question isn't stated clearly up front.
    • Results appear in the introduction before the method is defined.
    • Notation (mθ,mE,Iθ,Pm_θ, m_E, I_θ, P) is used before being introduced.
    • Terminology switches between "completion," "refill" and "concealment."
Questions for authors
  • Why only DiscoGP? Given the edge-only results in Table 1, should the claim be narrowed to weight-level masking methods?
  • Do circuits found on pretrained weights differ in any measurable way from random-weight circuits, such as overlap or out-of-distribution robustness? What evidence would show a circuit reflects pretraining?
  • Does the result hold on harder tasks, such as multi-token or many-candidate settings?
Reviewer_MYttOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
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Paper summary

The paper argues that circuit discovery methods that mask individual weights can construct task-functional circuits from randomised attention and MLP weights, challenging the “provenance assumption.” The experiments use DiscoGP on four models and three tasks, compare five pruning modes, and further investigate weight completion (concealment) and theoretical margin synthesis.

Critical strengths
  1. Interesting paper overall. Naming the "provenance assumption" is useful, and asking whether a discovered circuit reflects pretraining or the search procedure is a question worth raising.
  2. Good coverage across four models (GPT-2 Small/Medium, Pythia-410M, Qwen2.5-0.5B), three tasks, and five pruning modes. The granularity comparison provides useful evidence about the role of weight-level masking.
  3. The result that random-weight circuits are sparser in edges than pretrained ones is useful. It suggests that the circuit sparsity alone should not be read as evidence of learned structure.
  4. The theoretical intuition about cancellation vs. selection, is appreciated as it explains why scalar masks can construct favourable contributions from random weights, whereas edge masks can only select aggregate contributions.
Critical weaknesses
  1. Novelty is limited. Strong lottery ticket work (Ramanujan et al., 2020; Shen et al., 2021) already showed that masks over frozen random weights can solve tasks, including in Transformers. Shen et al. even consider pretrained embeddings with random Transformer weights. Random-network controls for masking-based interpretability also exist (Cao et al., 2021; Conmy et al., 2023). The main additions (to me) appear to be the provenance framing, the granularity comparison, and the completion/concealment experiments. How to distinguish the paper's core contribution more clearly from these existing results?

  2. It seems the claims are broader than the evidence. Edge-only discovery, which is closer to what mainstream circuit discovery methods use, underperforms on some original random-weight models in Table 1. Although fresh edge-only discovery succeeds after completion, those completed weights already incorporate task information through the earlier weight-mask optimisation. The results do not necessarily justify a broad “rethinking of circuit discovery,” especially given the strong lottery ticket literature.

  3. By freezing underlying weights, masking millions of scalar weights with gradient descent toward the correct answer is not it effectively learning a high-dimensional task-specific parameterization? Constructing a circuit is somewhat expected; the actual distinction between learning a mask and learning weights is important, but what are its interpretability implications?

  4. How to distinguish bw constructed circuits from extracted circuits? how much construction happens when discovering circuits in pretrained models?

  5. Do random-weight circuits still succeed under full-vocabulary KL, unseen templates, distribution shifts, or genuinely non-binary tasks?

  6. The notion of sparsity is somewhat misleading when considering the entire circuit: seeing results, it seems the circuits are sparse primarily in edges, not necessarily in parameters?

  7. The paper is hard to follow. It mixes three loosely connected threads: construction, concealment, and theory; in dense notation, which buries the main message. May be tightening it around the construction result and making the other two contributions clearly supporting arguments would help a lot.

Ref.:

https://aclanthology.org/2021.naacl-main.74 (Cao et al.)

https://arxiv.org/abs/2109.03939 (Shen et al.)

https://arxiv.org/abs/1911.13299 (Ramanujan et al.)

Questions for authors
  1. How do the authors distinguish the Lottery Circuit Hypothesis from existing strong lottery ticket results, particularly Shen et al. (2021), which already demonstrates useful random-weight Transformer subnetworks with pretrained embeddings? What is the central new finding beyond applying this observation to circuit discovery?

  2. Could the authors evaluate standard edge-only discovery under alternative interventions? How much of the reported advantage of weight-level masking depends on the particular zero-ablation setup?

  3. How dependent is successful construction on the retained pretrained components and the pooled-Gaussian randomisation?

  4. Do the constructed circuits generalise beyond the designated two-token comparisons?

  5. Given that weight-mask optimisation introduces millions of trainable binary decisions, how should its capacity be distinguished from ordinary supervised training?

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

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