ArXiv: 2601.19834

🎯 Pitch

Having AI generate images during reasoning delivers a 4× gain in sample efficiency for spatial tasks like paper folding—but shatters completely on grid-world puzzles, showing visual thinking is not a universal upgrade. The key is whether the task demands rich physical or 3D representations that words alone can’t efficiently capture.

1. Executive Summary

This paper presents the first principled study of when and how visual generation benefits reasoning through a visual superiority hypothesis: for tasks grounded in the physical world, visual generation more naturally serves as world models, whereas purely verbal world models encounter bottlenecks from representational limitations or insufficient prior knowledge. The authors formalize world modeling as a core component of chain-of-thought reasoning—decomposing it into two atomic capabilities, world simulation (predicting future states, e.g., unfolding paper step-by-step) and world reconstruction (inferring unseen views, e.g., novel-view synthesis of cube stacks)—and construct VisWorld-Eval, a seven-task evaluation suite spanning synthetic and real-world domains designed to isolate each capability. Using the unified multimodal model BAGEL-7B, interleaved verbal-visual chain-of-thought reasoning substantially outperforms purely verbal CoT on tasks requiring visual world modeling—achieving a 4× improvement in sample efficiency on paper folding and consistent gains on cube 3-view projection even for out-of-distribution stack sizes—while offering no clear advantage on grid-world tasks like mazes and Sokoban, establishing that visual generation benefits reasoning only when tasks demand richer spatial or physical representations than verbal world models can efficiently provide.

2. Context and Motivation

The Core Gap: We Don't Know When Visual Generation Actually Helps Reasoning

The fundamental question this paper tackles is deceptively simple: now that AI systems can generate both text and images within a single unified model, can visual generation actually make them reason better, and if so, when? This matters because the research community has raced to build unified multimodal models (UMMs) that seamlessly integrate language understanding with visual generation—models like BAGEL, Janus, Chameleon, and EMU3—with the implicit assumption that combining modalities must be beneficial. Yet, as the authors point out in Section 1, "the findings so far remain inconclusive. Reported empirical results are mixed, showing no consistent trends that visual generation reliably improves reasoning performance."

This gap is practically significant for several reasons the paper identifies:

  • Closing the human-AI gap in spatial and physical reasoning. Current large language models and vision-language models have achieved expert-level performance in formal domains like mathematics and programming (Guo et al., 2025; Trinh et al., 2024). Yet they "still lag far behind humans in domains like physical and spatial intelligence, which require richer representations and prior knowledge" (Section 1). The paper cites evidence that even young children naturally master basic physical and spatial intuition that state-of-the-art multimodal AI systems struggle with (Schulze Buschoff et al., 2025; Cai et al., 2025). This is not a niche limitation—it affects robotics, autonomous navigation, architectural reasoning, and any application where agents must interact with the physical world.

  • The emboodiment bottleneck. As the authors note in Section 6, "Artificial intelligence is increasingly being embodied in the physical world." Visual world modeling—the ability to mentally simulate spatial transformations, imagine occluded regions, and predict physical dynamics—is essential for embodied agents to plan, navigate, and manipulate objects. Without understanding when and how visual generation contributes to such modeling, developers building embodied AI systems lack principled guidance on architecture design and training data composition.

  • Unified model architecture justification. The field has invested substantial resources in building UMMs that model both verbal and visual modalities within a single backbone, using techniques ranging from discrete tokenization with autoregressive modeling (Chameleon, EMU3) to continuous tokenization with diffusion or flow matching (Transfusion, Janus, BAGEL). These architectural choices add significant complexity and training cost. Without clear evidence that visual generation reciprocally benefits reasoning—rather than just enabling better image generation from text instructions—the case for unified architectures over modular ones (e.g., a VLM that calls an external image generator) remains theoretically and economically shaky.

Conflicting Prior Evidence Creates Confusion, Not Consensus

The paper is motivated by a genuine empirical puzzle in the literature. Several recent works have explored whether visual generation enhances reasoning, but their results collectively fail to paint a coherent picture:

  • RealUnify (Shi et al., 2025) and Uni-MMMU (Zou et al., 2025) designed tasks where generation was expected to enhance reasoning but "report mixed results without revealing clear trends regarding the benefits of visual generation" (Section 2). This is the classic pattern of a field that lacks a theoretical framework: different tasks show different outcomes, and no one can explain why.

  • ROVER (Liang et al., 2025) goes further, revealing "fundamental limitations of current models in generating meaningful visual reasoning steps, often resulting in minimal or even negative gains in final accuracy" (Section 2). This is a stark cautionary tale: naive attempts to inject visual generation into reasoning can actually hurt performance. Yet ROVER's negative results don't tell us when visual generation might work—only that it often doesn't with current approaches.

  • MIRA (Zhou et al., 2025) takes an even more cautious approach, conducting what the authors call "a sanity test by providing manually annotated visual cues, thereby bypassing the evaluation of visual world modeling capability" (Section 2). In other words, MIRA tests whether having the right visual information helps reasoning, but doesn't test whether the model can generate that information itself. This is a crucial distinction: understanding that a diagram of a folded paper helps you solve the problem is different from being able to mentally unfold the paper yourself.

  • ThinkMorph (Gu et al., 2025) fine-tunes UMMs to reveal emergent reasoning behaviors but "restricts each CoT to a single intermediate image, thereby not fully exploiting the potential of interleaved CoT" (Section 2). This is a limitation because many reasoning tasks require step-by-step visual simulation—unfolding a paper one fold at a time, tracking a ball through multiple reflections, or constructing a cube stack view from partial information incrementally.

  • MVoT (Li et al., 2025) and VoT (Xu et al., 2025) explore "visualization-of-thought" where the model generates images as reasoning intermediates. While promising, these works study the phenomenon primarily in grid-world tasks like mazes and Sokoban, which this paper later shows are precisely the tasks where visual generation offers no clear advantage. This suggests that prior positive results may have been demonstrated on an unrepresentatively narrow and simple task distribution.

The net result is that a practitioner reading the literature would have no way to predict whether adding visual generation to their reasoning pipeline would help or hurt for their specific task. The field lacked an organizing principle.

Where Existing Approaches Fall Short

The paper identifies specific limitations in prior work that prevented progress toward a principled understanding:

No theoretical bridge between world models and reasoning. The concept of "world models" has a rich history in AI—from Ha and Schmidhuber (2018) through Dreamer (Hafner et al., 2025) to modern video generation models (Genie 3, Cosmos). Similarly, chain-of-thought reasoning has been extensively studied in LLMs. But these two literatures have developed largely in isolation. The world model literature focuses on learning compact representations of environment dynamics for planning and control, typically in reinforcement learning settings with explicit state spaces, actions, and rewards. The reasoning literature focuses on generating coherent text-based intermediate steps to improve final answer accuracy. No prior work had formally connected these concepts—showing how deliberate chain-of-thought reasoning can be understood as a process of explicitly maintaining and manipulating world model observations across reasoning steps.

Heuristic task design, not principled evaluation. As the authors state in Section 1, "the evaluation tasks used in current studies are designed heuristically, lacking a principled basis for understanding when and how visual generation can meaningfully contribute to multimodal reasoning." Prior benchmarks mixed different types of tasks without isolating what specific capability was being tested. For example, a benchmark might include both maze navigation (which primarily tests simple state tracking) and mental rotation of 3D objects (which tests complex spatial reasoning), but would report a single aggregate score. If visual generation helps with the 3D rotation task but not the maze task, the aggregate score conflates these effects and obscures the underlying pattern.

No analysis of why visual generation works when it works. The scattered positive results in the literature—a gain here, a failure there—lacked explanatory mechanisms. When visual generation improved performance on a task, was it because the model had stronger prior knowledge about visual transformations from pre-training? Because visual representations carry more information than verbal descriptions of the same scene? Because verbal reasoning introduced ambiguous descriptions that visual generation grounded concretely? Without answering these "why" questions, the field couldn't generalize findings to new tasks or guide architecture development.

Implicit assumption that more modalities = better reasoning. The prevailing intuition in multimodal AI has been that integrating more modalities improves performance—an intuition supported by successes in multimodal understanding (VLMs outperforming text-only models on vision-language tasks). But generation-for-reasoning is fundamentally different: the model must not only understand visual inputs but produce useful visual intermediates as part of its reasoning trajectory. This requires the model to know what to generate (which depends on the task) and how to generate it accurately (which depends on the model's visual generation fidelity). The assumption that visual generation capability automatically translates to reasoning benefits is underspecified and, as the negative results show, often false.

How This Paper Positions Itself

The paper frames its contribution through a world-model perspective that provides the missing theoretical scaffolding. This perspective draws on dual-coding theory from cognitive psychology (Paivio, 1990), which posits that the human mind processes information through two complementary codes—verbal and visual—that can function independently but often collaborate to support reasoning. The authors argue that current AI systems are missing the visual code, relying predominantly on verbal reasoning pathways, and that UMMs' visual generation capability offers a path to restoring this missing channel.

The paper's key positioning move is to reject the assumption that visual generation is universally beneficial and instead propose the visual superiority hypothesis: visual generation benefits reasoning specifically when tasks require (1) richer information than verbal descriptions can efficiently encode (solving the representational bottleneck problem) or (2) prior knowledge that is better learned from visual data than from text corpora (solving the prior knowledge gap problem). Conversely, when tasks have simple, fully-observable state spaces that can be compactly described in text—and when the model's text-based reasoning already encodes sufficient knowledge to solve them—visual generation provides no advantage and may even introduce additional errors from imperfect visual generation.

This hypothesis is formalized mathematically in Section 3 through two theorems. Theorem 1 decomposes the end-to-end reasoning error into reasoning errors and world-modeling errors, establishing a fundamental tradeoff: implicit world modeling (no explicit observations) avoids world-modeling errors but increases reasoning difficulty, while explicit world modeling (verbal or visual) reduces reasoning uncertainty at the cost of potential world-modeling errors. Theorem 2 bounds the benefit of explicit world modeling by both (i) how informative the observations are about underlying states and (ii) how much the reasoning step depends on those states. This provides a precise language for predicting when visual observations—which are highly informative about physical states but harder to model accurately—will outperform verbal observations, which are less informative but easier to generate faithfully.

The empirical contribution—VisWorld-Eval—is positioned not as yet another benchmark with heuristic task selection, but as a principled testbed that operationalizes the theoretical framework. Each task is designed to isolate a specific atomic world model capability (simulation or reconstruction) and to create conditions where the theoretical analysis predicts either a visual advantage or no advantage. The paper's experiments then test these predictions, using the same base model (BAGEL-7B) trained with different CoT formulations (implicit, verbal-only, interleaved verbal-visual) to enable controlled comparisons. This is in contrast to prior work that compared different models with different pre-training histories, making it impossible to attribute performance differences to the reasoning format rather than the underlying model.

The paper also connects to the broader AI ambition of general-purpose systems. By arguing that "complementary verbal and visual knowledge emerge from generative modeling across modalities, with the latter being especially valuable for bringing human-like intelligence into the physical world" (Section 1 conclusion), the authors position their work as an early step toward AI systems that reason with multimodal world models in the way humans do—not by replacing verbal reasoning but by augmenting it with visual simulation capabilities that are currently underdeveloped in AI. This framing distinguishes the paper from works that focus narrowly on benchmark performance and instead situates it within the grand challenge of building AI that truly understands and interacts with the physical world.

3. Technical Approach

This is a theoretical and empirical analysis paper whose core idea is that the value of visual generation for reasoning—specifically, generating images as intermediate steps in a chain-of-thought—is not universal but depends on whether the task demands richer representations or prior knowledge than verbal reasoning alone can provide, a claim the authors formalize through a world-model framework and test through controlled experiments on a purpose-built evaluation suite.

3.1 Reader Orientation

This paper constructs and validates a framework for deciding when to use visual generation during chain-of-thought reasoning. The system being analyzed is a unified multimodal model (UMM)—specifically BAGEL-7B—that can produce both text and images as outputs. The problem it addresses is a decision problem: given a reasoning task and a model capable of generating visual intermediates, should you have the model generate images as part of its reasoning steps, or should you stick to text-only reasoning? The shape of the solution is a theoretical decomposition of reasoning into world-modeling plus logical inference, combined with a purpose-built evaluation suite (VisWorld-Eval) where each task is designed to isolate a specific world-modeling capability, allowing controlled comparisons between visual, verbal, and implicit chain-of-thought formulations on the same base model.

3.2 Big-Picture Architecture (Diagram in Words)

The overall framework has four major components:

  1. Base Unified Multimodal Model (BAGEL-7B) — a pre-trained transformer that generates both text tokens autoregressively and image pixels via flow matching. It serves as the single neural substrate that can be post-trained to produce chain-of-thought reasoning in multiple modalities.

  2. Chain-of-Thought Formulations (3 variants) — three different ways to structure the reasoning process: (i) implicit world modeling, where the model reasons step-by-step without explicitly representing intermediate world states; (ii) verbal world modeling, where the model generates textual descriptions of intermediate states (e.g., symbolic matrices, coordinate lists); (iii) visual world modeling, where the model generates images of intermediate states interleaved with verbal reasoning steps. These are not separate models; they are different output formats trained via SFT on the same base model.

  3. VisWorld-Eval Task Suite — a collection of 7 tasks spanning both synthetic and real-world domains, each designed to isolate either the world simulation capability (predicting future states: paper folding, multi-hop manipulation, ball tracking, maze, Sokoban) or the world reconstruction capability (inferring unseen views: cube 3-view projection, real-world spatial reasoning). Each task has ground-truth answers enabling automated accuracy evaluation.

  4. Post-Training Pipeline (SFT + optional RL) — supervised fine-tuning on task-specific datasets with different CoT formats, followed optionally by reinforcement learning from verifiable rewards (RLVR) using GRPO. During RL, only verbal generation is optimized while visual generation is regularized via KL-divergence to the SFT reference model.

Information flows as follows: a task prompt (question + input images) enters the base model → the model generates a chain-of-thought in one of the three formats (implicit, verbal, visual) → the final answer is extracted and compared against ground truth → accuracy is computed per task and per CoT format.

3.3 Roadmap for the Deep Dive

  • First, the formal MOMDP formulation of world states and the two atomic capabilities—world reconstruction and world simulation—because these concepts define what "world modeling" means and what each task in VisWorld-Eval is designed to test.

  • Second, the chain-of-thought decomposition theorem and the visual superiority hypothesis, because these provide the theoretical language for predicting when visual generation should help, harm, or do nothing. Without this framework, VisWorld-Eval would be just another heuristic benchmark rather than a principled testbed.

  • Third, the VisWorld-Eval task suite construction, covering how each task was designed, what capability it isolates, how training and test data were generated, and what CoT templates were used. This is the operational bridge between theory and experiment.

  • Fourth, the model training protocol—SFT loss formulation, RL training with GRPO, and hyperparameters—because the controlled comparison between CoT formats depends on careful training to ensure differences arise from the reasoning format rather than training artifacts.

  • Fifth, the VLM comparison protocol and the probing methodology for implicit world models, because these address potential confounds (does BAGEL have weaker verbal reasoning than pure VLMs? do models learn implicit state representations that make explicit world modeling unnecessary for simple tasks?).

3.4 Detailed, Sentence-Based Technical Breakdown

3.4.1 The MOMDP Formulation: What Is a "World" in This Framework?

The paper grounds its entire analysis in a formal model of what a "world" is for a given task. This formalism is essential because the distinction between world simulation and world reconstruction—and the argument about which tasks benefit from visual generation—depends on a precise definition of states, observations, and transitions.

The MOMDP (Multi-Observable Markov Decision Process). The world of a specific task is formalized as $\mathcal{M} = (\mathcal{S}, \mathcal{A}, p, \Phi, \mathcal{O}_\phi, e_\phi)$, where:

  • $\mathcal{S}$ denotes the state space—the set of all possible underlying world configurations. In a paper-folding task, this would be the actual positions of folds, holes, and paper layers. In a cube-stacking task, this would be the 3D arrangement of cubes. Crucially, the state is typically hidden and not directly observable.

  • $\mathcal{A}$ denotes the action space—the set of possible operations that change the state. In paper folding, this would be folding actions (fold top half down, fold left third right). In ball tracking, this would be the ball's continuous motion and wall reflections.

  • $p$ is the transition function $s' \sim p(s' \mid s, a)$ that defines how the world evolves when an action is applied to a state. This captures the dynamics of the task—the physics of how paper unfolds, how balls bounce, how cubes stack.

  • $\Phi$ is the parameter space of observation functions—essentially, the set of all possible "viewpoints" or "rendering parameters" through which an underlying state can be perceived.

  • $\mathcal{O}_\phi$ is the observation space for a given observation parameter $\phi \in \Phi$. Different $\phi$ values produce observations in different modalities or from different perspectives. For example, $\phi$ might specify "front-right isometric view at 30° elevation" versus "top-down orthographic view" versus "English-language description focusing on object counts."

  • $e_\phi$ is the observation function $o = e_\phi(s) \in \mathcal{O}_\phi$ that maps an underlying state to a specific observation.

What this formalism captures. The key insight is that a single underlying world state can manifest as many different observations—visual observations corresponding to different camera poses, or verbal descriptions expressed with different emphases or styles. This maps directly to the human experience of mental models: when you mentally rotate an object, you're generating a new observation (the rotated view) from the same underlying 3D structure. When you mentally unfold a paper, you're simulating how the state evolves under unfolding actions and generating observations of the intermediate states.

The two-stage observation decomposition. The authors introduce a further refinement (in Appendix 7.1) that is critical for the theoretical analysis: each observation function is assumed to decompose into $e_\phi(s) = g_{\phi_m}(f_{\phi_s}(s))$, where:

  • $f_{\phi_s}$ is a modality-agnostic "slicing" function (parameterized by $\phi_s \in \Phi_s$) that extracts a partial view of the underlying state, retaining only the aspects of the state relevant to that particular observation. Think of this as "which part of the 3D structure is visible from this angle."

  • $g_{\phi_m}$ is a modality-specific "rendering" function (parameterized by $\phi_m \in \Phi_m$) that converts the sliced state information into a specific observation modality—rendering it as pixels for visual observations, or converting it to text descriptions for verbal observations.

This decomposition is what enables the theoretical comparison between visual and verbal world modeling: the sliced state $f_{\phi_s}(s)$ is the same regardless of modality, but the rendering $g_{\phi_m}$ differs. Visual rendering can encode more information (higher mutual information with the underlying state) but is harder to learn to generate accurately. Verbal rendering is lower-bandwidth but easier to model.

Why this formalism over alternatives. The authors explicitly note they set aside the debate between compact/abstract vs. comprehensive/high-fidelity world representations. By treating abstract observations (e.g., sketches, symbolic matrices) and high-fidelity observations (e.g., photorealistic renderings) as different view specifications $\phi$, the formalism accommodates both without committing to either. This is a pragmatic choice that allows the framework to apply across tasks ranging from simple grid-worlds (where a 2D coordinate list is a sufficient "observation") to complex 3D scenes (where only visual rendering captures all relevant spatial relationships).

3.4.2 Atomic Capabilities: World Simulation and World Reconstruction

Given the MOMDP formalism, the paper defines two fundamental capabilities that a world model must support, analogous to the operations humans perform in their mental models. These two capabilities form the organizing principle for VisWorld-Eval: every task in the evaluation suite is designed to primarily demand one of these two capabilities.

Capability 1: World Reconstruction. This is the ability to infer complete structure from partial observations and generate novel views of the same underlying state. Formally, the perception component of a world model encodes $n$ observations from limited views into an internal representation $\hat{s} = \text{enc}(o_{\phi_1}, \dots, o_{\phi_n}) \approx s$. This representation can then be decoded to generate an unseen observation: $\hat{o}_{\phi_{n+1}} = \text{dec}(\hat{s}, \phi_{n+1}) \approx e_{\phi_{n+1}}(s)$.

For modern generative models like UMMs, which do not have explicitly defined latent state representations, the world reconstruction capability is realized through end-to-end novel view generation:

pθ(oϕn+1∣oϕ1,…,oϕn)p_\theta(o_{\phi_{n+1}} \mid o_{\phi_1}, \dots, o_{\phi_n})

where $o_{\phi_1}, \dots, o_{\phi_n}$ are the given observations (e.g., input images from specific viewpoints), $o_{\phi_{n+1}}$ is the target observation (the novel view to be generated), and $p_\theta$ is the model's learned conditional distribution over observations.

What this equation computes: the probability of generating a particular observation $o_{\phi_{n+1}}$ from a novel viewpoint, conditioned on having seen $n$ observations from other viewpoints. The model implicitly learns to encode the underlying state from the input observations and decode it into the target viewpoint, without ever being explicitly trained to reconstruct a latent state vector.

Why this form: this end-to-end formulation avoids the need to define what the "state" is or to train an explicit encoder-decoder. It leverages the UMM's pre-trained ability to generate images conditioned on multimodal context. The cost is that there is no explicit guarantee the generated view is geometrically consistent with the inputs—the model might hallucinate details that are not supported by the provided observations.

Concrete example (cube 3-view projection): given an isometric view and two orthographic views of a cube stack, world reconstruction requires inferring the full 3D arrangement (which cubes are where, which are occluded) and then generating what the stack would look like from a fourth, unseen orthographic viewpoint. The input observations provide partial information; the model must fill in the rest using its prior knowledge about how 3D structures project to 2D views.

Capability 2: World Simulation. This is the ability to model dynamics and predict how the world evolves into the future. Formally, the prediction component of a world model predicts the next state from the current state and action: $\hat{s}' \sim \text{pred}(\hat{s}, a)$. For generative models without explicit states, this is realized through prediction of future observations:

pθ(ot+1∣o≤t,a≤t)p_\theta(o_{t+1} \mid o_{\leq t}, a_{\leq t})

where $o_{\leq t}$ are all observations up to time $t$, $a_{\leq t}$ are all actions taken up to time $t$, and $o_{t+1}$ is the next observation to be predicted.

What this equation computes: the probability of the next observation given the history of observations and actions. This is the generative-model equivalent of a dynamics model: rather than explicitly computing $s_{t+1} = f(s_t, a_t)$ and then rendering $o_{t+1} = e_\phi(s_{t+1})$, the model directly generates the next visual frame or verbal description.

Concrete example (paper folding): given the current folded state of a paper with holes punched in it, and the action "unfold the most recent fold," world simulation requires predicting what the paper looks like after that unfolding—where the holes end up, how the symmetry of the fold maps holes to new positions. A sequence of such predictions (unfold step 4, then unfold step 3, then unfold step 2, then unfold step 1) yields the fully unfolded state.

Concrete example (ball tracking): given the initial ball position, velocity vector, and the geometry of walls and holes, world simulation requires predicting the ball's trajectory—straight-line motion interrupted by specular reflections off walls—until it enters one of the numbered holes. This is a continuous dynamics problem that is naturally represented visually but would require precise coordinate tracking and trigonometric computations to represent verbally.

3.4.3 Chain-of-Thought as Explicit World Modeling

The paper's key theoretical move is to formalize chain-of-thought reasoning not as free-form text generation but as a process of explicitly maintaining and manipulating a sequence of world observations. The standard formulation of CoT as $R = \tau_1, \tau_2, \dots, \tau_H$ (a sequence of arbitrary intermediate steps) is refined to:

R=(r1,o1),(r2,o2),…,(rH,oH)R = (r_1, o_1), (r_2, o_2), \dots, (r_H, o_H)

where each reasoning step $\tau_i$ is decomposed into two components:

  • $r_i$ is a logical reasoning step based on accumulated context, typically expressed in text. This is the "thinking" part—the deduction, the planning, the decision about what to do next.

  • $o_i$ is the observation generated at that step—the world state after the reasoning step has been applied. The input images serve as the initial observation $o_0 = I$.

Subsequent observations $o_i$ are generated from previous reasoning and observations by invoking one of the two atomic world modeling capabilities: world reconstruction (Eq. 1, generating a novel view of the current state) or world simulation (Eq. 2, predicting the next state after an action). The reasoning steps $r_i$ implicitly specify which actions $a$ to apply and which view transformations $\phi$ to use.

What this formulation captures. This decomposition makes explicit something that is implicit in human reasoning: when we solve a spatial reasoning problem, we don't just think in words—we mentally "look at" the intermediate states, whether those are visual images, abstract diagrams, or spatial layouts. The verbal reasoning steps tell us what to do next ("now unfold the right half"), and the observations show us what the state looks like after doing it. In purely verbal CoT, the observations are text descriptions; in interleaved visual CoT, they are generated images.

The three CoT instantiations. Given this framework, the paper defines three concrete ways to implement chain-of-thought reasoning in a UMM:

  1. Implicit world modeling: $o_i = \emptyset$ for all $i$. No explicit observation is generated. The model reasons purely through the $r_i$ steps, encoding all state information implicitly in its hidden representations. This is how standard LLM CoT works—the model "keeps track" of where it is in the reasoning without writing down explicit state descriptions. The paper notes that "in practice, strictly distinguishing implicit from verbal world modeling can be difficult, because there are often partial descriptions of the current state in the reasoning part $r_i$." They treat verbal world modeling as the case where states are explicitly and completely expressed in text (e.g., full coordinate lists or symbolic matrices).

  2. Verbal world modeling: $o_i$ are verbal descriptions of the world state—character matrices for cube stacks, coordinate lists for maze positions, hole-count grids for paper folding. This makes the state tracking explicit but constrains it to the information bandwidth of natural language.

  3. Visual world modeling: $o_i$ are generated images—rendered views of the cube stack, diagrams of the partially unfolded paper, frames of the ball trajectory. This provides richer state information but requires the model to have both the prior knowledge to know what to generate and the generation fidelity to produce accurate images.

The CoT factorization for training. The model $p_\theta$ is factorized to reflect this decomposition:

pθ(R,A∣Q,I)=∏i=1H+1pθ(ri∣Ri)∏i=1Hpθ(oi∣R~i)p_\theta(R, A \mid Q, I) = \prod_{i=1}^{H+1} p_\theta(r_i \mid R_i) \prod_{i=1}^{H} p_\theta(o_i \mid \tilde{R}_i)

where $r_0 = Q$ (the question), $o_0 = I$ (the input images), $r_{H+1} = A$ (the final answer), and the prefixes are $R_i = (r_0, o_0, r_1, o_1, \dots, r_{i-1}, o_{i-1})$ and $\tilde{R}_i = (r_0, o_0, r_1, o_1, \dots, r_{i-1}, o_{i-1}, r_i)$. The first product runs over all reasoning steps plus the answer ($H+1$ terms), and the second product runs over the $H$ observation-generation steps.

What this factorization means operationally: the model first generates reasoning step $r_1$ conditioned on the question and input images. Then it generates observation $o_1$ conditioned on everything so far, including $r_1$. Then it generates $r_2$ conditioned on all previous text and observations. And so on, interleaving text generation and image generation until the final answer. For implicit world modeling, the observation terms $p_\theta(o_i \mid \tilde{R}_i)$ are omitted (or trivially $o_i = \emptyset$). For verbal world modeling, the observation terms generate text tokens. For visual world modeling, the observation terms generate image pixels via flow matching.

3.4.4 Theorem 1: Decomposing End-to-End Error into Reasoning and World-Modeling Errors

The first theoretical result provides the formal justification for why explicit world modeling can help: the end-to-end error of a chain-of-thought reasoning model decomposes into a sum of per-step reasoning errors and per-step world-modeling errors.

Theorem 1 statement. Let $p$ denote the distribution over optimal chain-of-thoughts and answers (the ground-truth reasoning process), and let $p_\theta$ be a learned reasoning model. Then:

KL⁡(p(A∣Q,I)∣∣pθ(A∣Q,I))≤∑i=1H+1Ep[KL⁡(p(ri∣Ri)∣∣pθ(ri∣Ri))]⏟reasoning errors+∑i=1HEp[KL⁡(p(oi∣R~i)∣∣pθ(oi∣R~i))]⏟world-modeling errors\operatorname{KL}(p(A \mid Q, I) \mid\mid p_\theta(A \mid Q, I)) \leq \sum_{i=1}^{H+1} \underbrace{\mathbb{E}_p\left[\operatorname{KL}(p(r_i \mid R_i) \mid\mid p_\theta(r_i \mid R_i))\right]}_{\text{reasoning errors}} + \sum_{i=1}^{H} \underbrace{\mathbb{E}_p\left[\operatorname{KL}(p(o_i \mid \tilde{R}_i) \mid\mid p_\theta(o_i \mid \tilde{R}_i))\right]}_{\text{world-modeling errors}}

where $\operatorname{KL}(\cdot \mid\mid \cdot)$ is Kullback-Leibler divergence (a measure of how different two probability distributions are), $A$ is the final answer, $Q$ is the question, $I$ is the input images, $H$ is the number of chain-of-thought steps, $R_i$ is the prefix of the CoT up to (but not including) reasoning step $r_i$, $\tilde{R}_i$ is the prefix up to and including $r_i$ but before observation $o_i$, and $r_{H+1} = A$.

What this inequality means in plain terms. The total error in the model's answer distribution (left side) is bounded by the sum of two types of per-step errors (right side):

  • Reasoning errors ($\operatorname{KL}(p(r_i \mid R_i) \mid\mid p_\theta(r_i \mid R_i))$): at each step $i$, how different is the model's distribution over the next reasoning step from the optimal distribution, given the history so far? This captures failures in logical deduction, planning, and decision-making.

  • World-modeling errors ($\operatorname{KL}(p(o_i \mid \tilde{R}_i) \mid\mid p_\theta(o_i \mid \tilde{R}_i))$): at each step $i$, how different is the model's distribution over the next observation from the optimal distribution, given the history including the just-generated reasoning step? This captures failures in accurately representing the world state—generating a wrong view of the cube stack, an incorrect unfolded paper diagram, or an inaccurate trajectory frame.

Why this decomposition matters. It reveals a fundamental trade-off in the choice of CoT formulation:

  • Implicit world modeling ($o_i = \emptyset$ for all $i$): the world-modeling error terms vanish entirely (there are no observations to get wrong), but this typically increases the reasoning errors because the model must implicitly encode and track all state information in its hidden representations. The $p_\theta(r_i \mid R_i)$ terms become harder to learn because the context $R_i$ contains less explicit state information.

  • Explicit world modeling (verbal or visual): introducing observations $o_i$ adds world-modeling error terms to the sum, but can reduce the reasoning errors by making the relevant state information explicitly available in the context. This is the classic trade-off between adding auxiliary prediction tasks (which introduce their own errors) and providing better features for the main task.

  • Visual vs. verbal world modeling: visual observations carry more information about the underlying state (higher $\mathbb{I}(o_i; s_i)$) than verbal descriptions of the same state, which can reduce reasoning errors more effectively. However, visual observations are typically harder to model accurately (higher world-modeling error) because image generation is more complex than text generation.

The inequality is derived via the data processing inequality (marginalizing out the intermediate chain-of-thought cannot increase the KL divergence) and the chain rule for KL divergence applied to the CoT factorization.

3.4.5 Theorem 2: Bounding the Benefit of Explicit World Modeling

The second theoretical result quantifies HOW MUCH explicit world modeling can help, and more importantly, what this benefit depends on.

Theorem 2 statement (part 1). For any observation modality, the reduction in reasoning uncertainty achieved by explicit world modeling is:

H(ri∣o0,r0:i−1)−H(ri∣Ri)=I(o1:i−1;ri∣o0,r0:i−1)≥0\mathbb{H}(r_i \mid o_0, r_{0:i-1}) - \mathbb{H}(r_i \mid R_i) = \mathbb{I}(o_{1:i-1}; r_i \mid o_0, r_{0:i-1}) \geq 0

where $\mathbb{H}(\cdot)$ is Shannon entropy (a measure of uncertainty), and $\mathbb{I}(\cdot; \cdot \mid \cdot)$ is conditional mutual information (how much information one variable provides about another, given a third).

What this computes: the left side is the difference between two entropies. The first term $\mathbb{H}(r_i \mid o_0, r_{0:i-1})$ is the uncertainty about reasoning step $r_i$ when we only have the input observation $o_0$ and the previous reasoning steps $r_{0:i-1}$—this is the implicit world modeling case, where no intermediate observations are generated. The second term $\mathbb{H}(r_i \mid R_i)$ is the uncertainty when we additionally have all the intermediate observations $o_1, \dots, o_{i-1}$ in the context—this is the explicit world modeling case. The difference equals the mutual information between the intermediate observations and the current reasoning step, conditioned on the initial information.

Why this is non-negative: mutual information is always non-negative. This formalizes the intuitive claim that adding explicit observations to the context cannot increase uncertainty about the next reasoning step—at worst, it provides no new information. In practice, of course, if the generated observations are wrong (high world-modeling error from Theorem 1), they could mislead the reasoner. Theorem 2 assumes perfect world modeling; Theorem 1 accounts for the cost of imperfect world modeling.

Theorem 2 statement (part 2). The reduction in reasoning uncertainty is bounded by:

I(o1:i−1;ri∣o0,r0:i−1)≤min⁡(I(o1:i−1;s1:i−1),I(ri;s0:i−1,r0:i−1))\mathbb{I}(o_{1:i-1}; r_i \mid o_0, r_{0:i-1}) \leq \min\left(\mathbb{I}(o_{1:i-1}; s_{1:i-1}), \mathbb{I}(r_i; s_{0:i-1}, r_{0:i-1})\right)

where $s_{1:i-1}$ are the latent states associated with observations $o_{1:i-1}$.

What this upper bound means, term by term:

  • First term $\mathbb{I}(o_{1:i-1}; s_{1:i-1})$: how much information do the observations provide about the underlying states? This is a measure of observation fidelity or expressiveness. Visual observations typically have high values here—a rendered image of a cube stack contains much more information about the 3D arrangement than a verbal description like "blue cube on red cube on green cube." This term captures the representational bottleneck argument: if observations are low-information (like text descriptions), they cannot reduce reasoning uncertainty much regardless of how accurate they are.

  • Second term $\mathbb{I}(r_i; s_{0:i-1}, r_{0:i-1})$: how much does reasoning step $r_i$ depend on the underlying states, given the reasoning history? This is a measure of state-dependence of the reasoning task. If the next reasoning step is essentially determined by the previous reasoning steps alone (e.g., "2 + 2 = 4" doesn't depend on any world state), then even perfect world modeling provides no benefit. This term captures the idea that world modeling only helps for tasks where the reasoning genuinely depends on tracking the evolving state.

The min operation: the benefit of explicit world modeling is limited by whichever of these two bounds is tighter. If the observations carry little state information (low first term), the benefit is capped regardless of how state-dependent the reasoning is. If the reasoning barely depends on the state (low second term), the benefit is capped regardless of how informative the observations are.

Why this form matters for the visual superiority hypothesis. The theorem provides a precise language for predicting when visual generation will help:

  • When visual generation should help: tasks where (1) $\mathbb{I}(o_i^{\text{visual}}; s_i) \gg \mathbb{I}(o_i^{\text{verbal}}; s_i)$ (visual observations carry substantially more state information than verbal ones) AND (2) $\mathbb{I}(r_i; s_{0:i-1}, r_{0:i-1})$ is large (the reasoning depends heavily on the tracked state). Paper folding, ball tracking, and cube 3-view projection fit this profile: the spatial state is rich and hard to verbalize precisely, and the reasoning critically depends on tracking exactly where holes are or how cubes are arranged.

  • When visual generation should not help: tasks where either $\mathbb{I}(o_i^{\text{visual}}; s_i) \approx \mathbb{I}(o_i^{\text{verbal}}; s_i)$ (verbal descriptions capture essentially the same state information as visual ones) OR $\mathbb{I}(r_i; s_{0:i-1}, r_{0:i-1})$ is small (the reasoning doesn't depend much on the state). Maze and Sokoban fit the first profile: the state is just a 2D coordinate, which a text description like "(3, 4)" captures as completely as an image of a grid.

The proof in Appendix 7.1 uses properties of ternary mutual information and the conditional independence $r_i \perp o_{1:i-1} \mid s_{1:i-1}$ (reasoning steps depend on observations only through the underlying states they reveal).

3.4.6 The Visual Superiority Hypothesis (Formal Statement)

Drawing on the theoretical analysis, the paper states its central hypothesis in terms of two factors that make visual world modeling superior:

Factor 1: Informativeness. "While verbal and symbolic representations capture high-level semantic abstractions, they often suffer from ambiguity and representational bottlenecks. In contrast, visual observations are more concrete and information-rich, directly encoding physical properties such as motion and spatial relationships." Formally, this means $\mathbb{I}(o_i^{\text{visual}}; s_i) > \mathbb{I}(o_i^{\text{verbal}}; s_i)$ for many physical and spatial tasks—visual observations have higher mutual information with the underlying state than verbal descriptions.

Factor 2: Prior knowledge. "Visual world knowledge is inherently complementary to symbolic knowledge. Humans and animals acquire much of this knowledge (e.g., physical interactions and spatial transformations) through perception, largely independent of language." The paper formalizes this through a transfer learning analysis (Theorem 6 in Appendix 7.2): the distribution shift $\text{TV}(P, Q)$ between pre-training data $P$ and downstream task data $Q$ varies across modalities. If a task's required knowledge (e.g., how folded paper unfolds) is well-represented in visual pre-training data (e.g., videos of folding/unfolding) but poorly represented in text pre-training data (e.g., detailed step-by-step unfolding descriptions), then visual world modeling will exhibit smaller distribution shift and better post-training sample efficiency.

The formal bound in Theorem 6 states that the excess risk after fine-tuning is:

EQ(θQ)≤2εgen+LQ(4μTV(P,Q)−r)+\mathcal{E}_Q(\theta_Q) \leq 2\varepsilon_{\text{gen}} + L_Q\left(\sqrt{\frac{4}{\mu}\text{TV}(P, Q)} - r\right)_+

where $\varepsilon_{\text{gen}}$ is a generalization error term that decreases with more fine-tuning data, $L_Q$ is a Lipschitz constant for the loss, $\mu$ is a local strong convexity parameter, $\text{TV}(P, Q)$ is the total variation distance between pre-training and downstream distributions, and $r$ is the radius of the fine-tuning constraint set (how far parameters can move from the pre-trained model).

What this bound says operationally: larger distribution shift $\text{TV}(P, Q)$ increases the bias term in the excess risk, meaning the model needs more fine-tuning data $n$ (to reduce $\varepsilon_{\text{gen}}$) to achieve the same performance. If visual world modeling has smaller $\text{TV}(P, Q)$ for a given task (because the relevant knowledge was better represented in visual pre-training), it will be more sample-efficient during post-training.

3.4.7 The VisWorld-Eval Task Suite: Design Principles

The paper constructs VisWorld-Eval to operationalize the theoretical framework. Each task is designed, not chosen heuristically, to isolate one of the two atomic world modeling capabilities and to create conditions where the theoretical analysis makes specific predictions about visual generation benefits.

Task categorization. Tasks are assigned to world simulation (predicting future states given actions) or world reconstruction (inferring unseen views from partial observations):

  • World simulation tasks:

    • Paper folding (unfolding sequence)
    • Multi-hop manipulation (object addition/removal/color change sequence)
    • Ball tracking (physical trajectory simulation)
    • Maze (grid-world navigation)
    • Sokoban (grid-world puzzle solving)

  • World reconstruction tasks:

    • Cube 3-view projection (novel viewpoint synthesis from 3 input views)
    • Real-world spatial reasoning (camera/object positional relationships from multiple views)

What makes these tasks principled (not heuristic). For each task, the paper explicitly identifies which factor of the visual superiority hypothesis applies:

  • Paper folding: simulation task, visual advantage from both information richness (the contour of the paper during unfolding is hard to describe precisely in text) and prior knowledge (geometric symmetry and spatial transformations are abundantly demonstrated in visual data like images and videos).

  • Multi-hop manipulation: simulation task, visual advantage primarily from information richness (precisely tracking object positions and spatial relationships through coordinate arithmetic without external tools is difficult and error-prone for language models).

  • Ball tracking: simulation task, visual advantage from both information richness (continuous trajectory with specular reflections is extremely awkward to represent verbally, requiring trigonometric calculations) and prior knowledge (physical dynamics of elastic collisions are naturally learned from visual experience).

  • Cube 3-view projection: reconstruction task, visual advantage primarily from prior knowledge ("visually rotating objects has been a rich experience during pre-training with large-scale Internet videos," while reasoning about character matrices representing cube stacks has limited pre-training coverage).

  • Real-world spatial reasoning: reconstruction task, visual advantage from both information richness (fully describing a novel view of a realistic scene in text is "similarly ill-suited") and the grounding effect (visual generation reduces hallucinations in spatial reasoning by tying the model's claims to concrete generated images).

  • Maze and Sokoban: simulation tasks, predicted to show NO visual advantage because state tracking is "relatively simple, typically requiring the maintenance of only one or two two-dimensional coordinates, which can be adequately handled through verbal reasoning alone." The states are fully observable and deterministic, meaning Corollary 1 of the theoretical analysis applies: explicit world modeling provides no additional benefit in the infinite-data/capacity limit.

Test prompt difficulty calibration. For each task, test prompts are constructed at specific difficulty levels:

  • Paper folding: maximum difficulty (grid size 8 with 4 folding steps).
  • Ball tracking: cases where the ball reflects off at least one wall before entering a hole (non-trivial trajectories).
  • Cube 3-view: grid sizes randomly sampled from 3–5, with stack size 6 used for out-of-distribution evaluation.
  • Maze: fixed 5×5 grid size.
  • Multi-hop manipulation: varying initial objects (3–6) and operation frequencies (1–5 of each type).

SFT data construction pipeline. For each task, the authors generate chain-of-thoughts using a multi-stage process:

  1. Rule-based template generation: for tasks with well-defined solution procedures (paper folding, cube 3-view, maze, multi-hop manipulation), a deterministic procedure is defined—e.g., "unfold step-by-step from most recent fold to earliest, then count holes by shape." This produces a skeleton CoT.

  2. LLM rewriting: the skeleton CoTs are "rewritten with Gemini 2.5 Pro to improve clarity and logical coherence" (or, for ball tracking and Sokoban, CoTs are generated by Seed 1.6 explaining dynamics between frames). This step is crucial: it converts mechanical templates into natural-sounding reasoning while preserving the correct logical structure.

  3. Modality-specific formatting: under visual world modeling, intermediate rendered states (images of partially unfolded paper, frames of ball trajectory, novel cube views) are interleaved with verbal reasoning steps. Under verbal world modeling, the same intermediate states are represented using text formats—matrices encoding grid coverage and hole shapes for paper folding, character matrices for cube stacks, coordinate lists for maze positions. Under implicit world modeling, explicit state tracking is removed (for Maze and Sokoban) or coordinates are masked with special tokens [masked].

SFT data statistics (Table 2 in Appendix).

TaskTraining SamplesTest Samples
Paper folding2,357480
Multi-hop manipulation2,000480
Ball tracking2,2541,024
Maze8,448480
Sokoban7,715480
Cube 3-view projection2,500480
Real-world spatial reasoning10,661522

The much larger training sets for Maze and Sokoban reflect data augmentation (randomized detours, varied grid configurations) rather than inherent task complexity.

3.4.8 Model Training: SFT Loss Formulation

The base model is BAGEL-7B-MoT (Deng et al., 2025), described as "a state-of-the-art open-source unified multimodal model." The paper deliberately chooses to post-train (SFT) a UMM rather than evaluate zero-shot because "no open-source model has been natively optimized for interleaved verbal-visual generation for reasoning" and "even commercial closed-source models currently exhibit fundamental limitations in generating visual intermediate reasoning steps." Post-training provides "a more meaningful estimate of the upper bound for multimodal reasoning performance."

SFT loss for visual world modeling CoT:

Lθ(Q,I,R,A)=−∑i=1H+1∑j=1∣ri∣log⁡pθ(ri,j∣ri,<j,Ri)+∑i=1HEt,ϵ∥vθ(oit,t∣R~i)−(ϵ−oi)∥22\mathcal{L}_\theta(Q, I, R, A) = -\sum_{i=1}^{H+1} \sum_{j=1}^{|r_i|} \log p_\theta(r_{i,j} \mid r_{i,<j}, R_i) + \sum_{i=1}^{H} \mathbb{E}_{t, \epsilon} \left\| v_\theta(o_i^t, t \mid \tilde{R}_i) - (\epsilon - o_i) \right\|_2^2

where:

  • $\theta$ are the model parameters being optimized.
  • $Q$ is the question, $I$ are input images, $R$ is the chain-of-thought, $A$ is the answer.
  • $H$ is the number of CoT steps.
  • $r_{i,j}$ is the $j$-th token of reasoning step $r_i$.
  • $|r_i|$ is the number of tokens in step $r_i$.
  • $r_{i,<j}$ are the tokens of step $r_i$ before position $j$.
  • $R_i = (r_0, o_0, \dots, r_{i-1}, o_{i-1})$ is the prefix context before generating $r_i$.
  • $\tilde{R}_i = (r_0, o_0, \dots, r_{i-1}, o_{i-1}, r_i)$ is the context before generating observation $o_i$.
  • $o_i^t = t o_i + (1-t)\epsilon$ is a noisy version of the target image $o_i$, with $t \in [0,1]$ uniformly sampled and $\epsilon \sim \mathcal{N}(0, I)$.
  • $v_\theta$ is the learned velocity field (flow matching model) that predicts the direction from noise to data.

What this loss computes, term by term:

  • First term (autoregressive language modeling loss): for each reasoning step $i$ and answer step $r_{H+1}$, and for each token $j$ within that step, the model maximizes the log-probability of the correct next token given all previous tokens and observations. This is standard cross-entropy for text generation, applied sequentially to each reasoning step conditioned on the full multimodal history.

  • Second term (flow matching loss for image generation): for each observation step $i$, the model learns to generate the image $o_i$ via flow matching. Given a noisy version of the target image $o_i^t$, the model's velocity field $v_\theta$ predicts the direction $\epsilon - o_i$ (from the noise $\epsilon$ toward the clean image $o_i$). The expectation is over the timestep $t$ and noise $\epsilon$. The squared L2 norm measures prediction error.

Why this combined loss: the autoregressive term handles all text generation (reasoning steps and final answer), while the flow matching term handles all image generation (intermediate observations). The two terms are coupled because the flow matching term conditions on $\tilde{R}_i$, which includes the just-generated reasoning step $r_i$. This means the model learns an interleaved generation process: first decide what to do (generate $r_i$), then visualize the result (generate $o_i$), rinse and repeat.

Training hyperparameters (Table 3 in Appendix):

  • Learning rate: $3 \times 10^{-5}$
  • LR Schedule: Constant
  • Optimizer: AdamW
  • Loss weight ratio (CE:MSE): 1:10 (the flow matching loss is weighted 10× higher than the language modeling loss)
  • Warm-up steps: 200
  • Training steps: 4000
  • Generation resolution: (256, 1024) for paper folding and cube 3-view; (240, 1024) for multi-hop manipulation; (256, 512) for all other tasks
  • Understanding resolution: (224, 980) across all tasks
  • Sequence length per rank: 32K tokens
  • Number of ranks: 8

Design choice: asymmetric loss weighting (CE:MSE = 1:10). The flow matching loss for image generation is weighted 10× higher than the language modeling loss. This likely reflects that image generation is inherently harder to learn (higher-dimensional output space) and that the base model's language capabilities are already strong, so the language loss needs less emphasis during SFT. Without this asymmetry, the model might prioritize maintaining text coherence at the expense of learning accurate visual generation.

Design choice: different generation resolutions per task. Paper folding and cube 3-view use wider aspect ratios (256×1024) because their visual states benefit from panoramic rendering (unfolded paper is wide; cube stack views are square-ish but rendered with surrounding context). Multi-hop manipulation uses 240×1024 for similar reasons (wide scenes with multiple objects). Other tasks use more standard 256×512, sufficient for grids and trajectories.

Design choice: constant learning rate schedule. Rather than cosine decay or step decay, the authors use a constant learning rate throughout 4000 steps. With only 4000 total steps and a warm-up of 200, this is essentially a short fine-tuning run where the learning rate is kept high enough to adapt to the task-specific format without decaying before convergence.

3.4.9 Model Training: RLVR with GRPO

After SFT, the paper optionally applies reinforcement learning from verifiable rewards (RLVR) using Group Relative Policy Optimization (GRPO), following the approach of DeepSeek-R1 (Guo et al., 2025).

RL training objective for interleaved CoT:

Jθ(Q,I)=Eo,r∼pθold[∑i=1H+1∑j=1∣ri∣(min⁡(pθ(ri,j∣ri,<j,Ri)pθold(ri,j∣ri,<j,Ri)A,clip(pθ(ri,j∣ri,<j,Ri)pθold(ri,j∣ri,<j,Ri),1−ε,1+ε)A))−∑i=1HEt,ϵ∥vθ(oit,t∣R~i)−vθref(oit,t∣R~i)∥22]\mathcal{J}_\theta(Q, I) = \mathbb{E}_{o, r \sim p_{\theta_{\text{old}}}} \Bigg[ \sum_{i=1}^{H+1} \sum_{j=1}^{|r_i|} \Bigg( \min\Big( \frac{p_\theta(r_{i,j} \mid r_{i,<j}, R_i)}{p_{\theta_{\text{old}}}(r_{i,j} \mid r_{i,<j}, R_i)} A, \text{clip}\Big( \frac{p_\theta(r_{i,j} \mid r_{i,<j}, R_i)}{p_{\theta_{\text{old}}}(r_{i,j} \mid r_{i,<j}, R_i)}, 1-\varepsilon, 1+\varepsilon\Big) A \Big) \Bigg) - \sum_{i=1}^{H} \mathbb{E}_{t, \epsilon} \left\| v_\theta(o_i^t, t \mid \tilde{R}_i) - v_{\theta_{\text{ref}}}(o_i^t, t \mid \tilde{R}_i) \right\|_2^2 \Bigg]

where:

  • $p_{\theta_{\text{old}}}$ is the policy from the previous iteration (for sampling rollouts).
  • $A$ is the advantage (determined by reward comparison within a group of sampled responses; see GRPO for details—typically, reward = 1 if answer is correct, 0 otherwise).
  • $\varepsilon$ is the PPO clipping parameter.
  • $v_{\theta_{\text{ref}}}$ is the velocity field of the SFT-trained reference model (frozen during RL).
  • All other notation is as in the SFT loss.

What this objective computes, term by term:

  • First term (clipped policy gradient on text tokens): for each reasoning step and answer token, the model updates its text-generation policy using a PPO-style clipped objective. The probability ratio $p_\theta / p_{\theta_{\text{old}}}$ is multiplied by the advantage $A$, and the result is clipped to $[1-\varepsilon, 1+\varepsilon]A$ to prevent destabilizingly large policy updates. The $\min$ operation selects the more conservative of the clipped and unclipped objectives (standard PPO).

  • Second term (KL regularization on visual generation): the model's visual generation velocity field $v_\theta$ is regularized toward the SFT reference model's velocity field $v_{\theta_{\text{ref}}}$ via squared L2 distance, weighted by expectation over timestep and noise. This ensures the visual generation capability is preserved during RL rather than being overwritten by the text-focused reward signal.

Critical design choice: only verbal generation is optimized by RL. As stated explicitly in Section 4.2, "only the verbal generation component is optimized by GRPO, while visual generation is regularized via the KL-divergence with respect to the SFT-trained reference model." The justification is both practical and conceptual: the verifiable reward (answer correctness) provides a direct signal for improving verbal reasoning (which determines the final answer), but there is no similarly direct reward signal for intermediate visual generation quality. Without explicit per-step visual accuracy rewards, optimizing visual generation via RL could lead to degeneration. The KL penalty acts as a "stay close to what we know works" constraint.

RL training hyperparameters (Table 4 in Appendix):

  • Learning rate: $1 \times 10^{-5}$
  • Batch size: 128
  • GRPO mini batch size: 32
  • Group size: 16
  • KL loss coefficient for visual generation: 0.1
  • KL loss coefficient for verbal generation: 0.0

Design choice: KL coefficient of 0.0 for verbal generation. The verbal generation component is not regularized to stay close to the SFT model—it is allowed to freely adapt based on the reward signal. Only visual generation is constrained. This reflects the asymmetry of the task: answer correctness depends on verbal reasoning quality (which RL should improve) while depending on visual generation only indirectly (as a helpful but not directly rewarded auxiliary).

Design choice: group size 16. GRPO compares responses within groups of 16 sampled completions for the same prompt. The advantage for each token is based on how its response's reward compares to the mean reward within its group, rather than requiring a separately learned value function (as in standard PPO). This makes the training simpler and more stable for tasks with binary (correct/incorrect) rewards.

3.4.10 VLM Comparison and Confound Control

To address the concern that "UMMs are typically trained with a stronger emphasis on visual generation, which could compromise verbal reasoning capabilities, and bias comparisons in favor of visual world modeling," the paper runs a controlled comparison:

Baseline model: Qwen2.5-VL-7B-Instruct, which shares the same Qwen 2.5 LLM base model as BAGEL's language backbone, but lacks native image generation capability. This is a pure vision-language model (VLM) that can understand images and generate text, but cannot produce images as outputs.

Training protocol: Qwen2.5-VL is fine-tuned on the same verbal CoT datasets used for BAGEL's verbal and implicit world modeling experiments, on three representative tasks (paper folding, cube 3-view projection, and multi-hop manipulation).

What this comparison tests: if BAGEL's visual world modeling advantage were an artifact of weakened verbal reasoning (compared to a pure VLM), then Qwen2.5-VL should outperform BAGEL on the verbal CoT conditions. If the visual advantage is genuine, then:

  1. Qwen2.5-VL's verbal CoT performance should be comparable to BAGEL's verbal CoT performance (confirming no verbal reasoning deficit in BAGEL).
  2. BAGEL's visual CoT performance should exceed both Qwen2.5-VL's verbal CoT and BAGEL's own verbal CoT (confirming the benefit comes from the visual modality, not from model-specific factors).

The paper reports that "the SFT performance of Qwen2.5-VL with implicit and verbal world modeling is comparable to that of BAGEL, without exhibiting significant advantages," supporting the conclusion that the visual advantage is real rather than an artifact of compromised verbal reasoning.

3.4.11 Probing Implicit World Models in the Maze Task

For the maze task—where visual generation provides no advantage over implicit or verbal CoT—the paper conducts a probing experiment to investigate whether the model learns implicit representations of the maze state even without explicit state tracking.

Probing methodology:

  1. Model variants examined: three versions of BAGEL-7B with identical architecture but different weights:

    • A randomly initialized (untrained) model.
    • The pre-trained BAGEL-7B-MoT model (before any task-specific SFT).
    • The model after SFT on maze CoT data in implicit world modeling format—where all explicit point coordinates during reasoning are replaced with placeholder tokens [masked].

  2. Representation extraction: for each model, the hidden representations at each transformer layer are extracted specifically at the positions of the [masked] tokens in the reasoning text. These tokens are the only locations where coordinate information could be implicitly encoded, since the surrounding text only provides directional reasoning ("go up," "turn right") without explicit coordinates.

  3. Probe training: two-layer MLPs (hidden size 4096) are trained on these extracted representations to predict the ground-truth point coordinates at each reasoning step. Since all mazes are 5×5, coordinate prediction is formulated as two independent 5-way classification tasks (one for x-coordinate, one for y-coordinate). The training/validation split is 80/20.

  4. Accuracy measurement: classification accuracy is computed separately for x and y, and the average of the two is reported as the overall prediction accuracy.

What this experiment reveals (Figure 6c):

  • Random model: achieves only random-guess accuracy (~20% for 5-way classification). Confirms that the probing methodology is valid—without any learning, representations contain no coordinate information.

  • Pre-trained model: already exhibits "emergent representations that are predictive of maze states." The prediction accuracy is substantially above random chance, indicating that BAGEL's pre-training on diverse multimodal data has endowed it with some ability to track spatial state implicitly, even without task-specific training.

  • Non-monotonic layer trend: prediction accuracy increases from lower layers (which capture low-level features) to middle layers, and then decreases toward the final layers. The authors interpret this as: middle layers are "likely specialized" for representing task-relevant state information, while final layers focus on next-token prediction and may discard or transform the state representation into a format optimized for generating the next output token.

  • SFT model: supervised fine-tuning on maze CoT data—despite providing NO explicit coordinate supervision (all coordinates are masked)—"substantially enhances this internal predictability, achieving near-perfect accuracy" in coordinate prediction from the probe.

What this implies for the main results. The probe experiment explains why visual world modeling provides no advantage for mazes: the model already learns to track the maze state internally (in its hidden representations) even without explicit observations. Implicit world modeling is sufficient because the state space is simple enough (5×5 grid, two coordinates) to be encoded in hidden activations. Adding explicit verbal coordinates or visual grid renderings provides redundant information, increasing world-modeling error (from Theorem 1) without reducing reasoning uncertainty (since the implicit representation already captures all needed state information).

This is a concrete instantiation of Corollary 1 (Appendix 7.1): in deterministic, fully observable environments with sufficient model capacity, "explicit world modeling provides no additional benefit" because the implicit representation already captures the state.

Limitations acknowledged. The authors note this analysis is "intriguing but preliminary" and express interest in extending the probing approach to compare VLMs and UMMs, hypothesizing that UMMs may "capture complementary aspects of world knowledge through training for multimodal generation" that manifest in different representational geometries.

4. Key Insights and Innovations

Innovation 1: Difficulty-Conditioned World-Modeling as a Replacement for Heuristic Task Selection

The paper's most fundamental conceptual contribution is not a new model, training procedure, or benchmark, but rather a diagnostic framework that replaces the field's heuristic approach to evaluating visual generation for reasoning. Prior work selected tasks based on intuition or availability—including visual jigsaws, mazes, or general STEM questions—without articulating why visual generation should help on some tasks and not others. This produced the confused empirical landscape the paper inherits: RealUnify and Uni-MMMU reported mixed results, ROVER found negative effects, and ThinkMorph showed emergent behaviors only under restricted conditions. Each paper tested different tasks on different models, and the field had no shared language to reconcile the contradictory outcomes.

The paper's diagnostic innovation is to ask, for any proposed task, two precise questions: (1) does the task's state carry substantially more information in visual form than in verbal form (the informativeness criterion), and (2) has the model seen sufficient examples of the relevant transformations in visual pre-training data to generate them faithfully (the prior knowledge criterion)? These questions operationalize the theoretical bounds from Theorem 2—the first term captures informativeness, the second captures the transfer learning analysis—into a practical checklist for task design. The paper then demonstrates the framework's productivity by constructing VisWorld-Eval, where each task is selected specifically to produce a predicted outcome under this analysis: visual generation should help on paper folding and ball tracking (high informativeness, strong visual priors), should not help on mazes and Sokoban (low informativeness gap, sufficient verbal/implict state tracking), and so on.

This is a fundamental shift, not an incremental refinement. Before this paper, the question "does visual generation help reasoning?" was asked as a binary, universal question. The answer was assumed to be discoverable by running experiments on heuristically chosen tasks and reporting aggregate accuracy. The paper's reframing makes the question conditional: "for which tasks, under which conditions on state complexity and pre-training coverage, does visual generation help reasoning?" The experimental results—substantial gains on paper folding and cube projection, no gains on mazes and Sokoban—validate the framework's predictive power. Moreover, the probing experiment (Figure 6c) provides a mechanistic explanation for why the no-gain prediction holds for mazes: the model already encodes sufficient state information implicitly, making explicit world modeling redundant. This closes the loop from theoretical prediction to empirical verification to mechanistic explanation, something no prior work in this area had achieved.

The practical implication is that future benchmarks for multimodal reasoning should be designed with this diagnostic framework in mind—not by aggregating conveniently available tasks, but by deliberately varying informativeness gap and prior knowledge alignment to map out the boundaries of visual generation's utility.

Innovation 2: The World-Model Decomposition as a Theoretical Bridge Between Two Disconnected Literatures

The paper constructs a formal bridge between two research communities that have largely operated in isolation: the world model literature in reinforcement learning and the chain-of-thought reasoning literature in language models. This bridge is the decomposition of chain-of-thought into interleaved reasoning steps and world observations (Section 3.3), formalized in the factorization $R = (r_1, o_1), (r_2, o_2), \dots, (r_H, o_H)$.

Prior world model work (Ha and Schmidhuber, 2018; Hafner et al., 2025; video generation models like Genie 3 and Cosmos) focuses on learning compact dynamics models for planning and control in embodied settings, typically with explicit state spaces, action spaces, and rewards defined by the environment. These models are evaluated on their ability to predict future observations or enable sample-efficient policy learning. Conversely, the CoT literature (Wei et al., 2022; Guo et al., 2025) studies how generating intermediate text steps improves final answer accuracy on reasoning benchmarks, but treats those intermediate steps as unstructured text—there is no notion of an "observation" of an underlying state, no decomposition into world modeling versus logical inference.

The paper's decomposition connects these worlds by arguing that every CoT reasoning step implicitly invokes a world model operation. When a model reasons about unfolding paper, the step "now let's see where the holes are after the third unfold" is a request to the world model to simulate the unfolding dynamics and produce an observation of the result. The reasoning text $r_i$ specifies the operation; the generated observation $o_i$ is the world model's output. This reframing has several intellectual consequences that go beyond the paper's empirical results:

  • It provides a unified error taxonomy (Theorem 1): end-to-end failure can now be decomposed into reasoning errors (the model chose the wrong logical step) and world-modeling errors (the model chose the right step but generated an inaccurate observation of the result). This taxonomy is actionable—it tells practitioners whether to invest in better reasoning training data or better world model fidelity.

  • It explains why scale alone hasn't solved spatial reasoning. Even very large language models struggle with physical and spatial reasoning (Schulze Buschoff et al., 2025; Cai et al., 2025) because scaling up text-based pre-training improves the reasoning component of Theorem 1's decomposition but does nothing to improve the visual world-modeling component, which requires visual training data. The paper's argument that "different aspects of world knowledge are concentrated in different data modalities" is not just an intuition—it follows from the factorization: the $p_\theta(o_i \mid \tilde{R}_i)$ terms are learned from visual generation training, and if that training is insufficient for a task's required transformations, no amount of verbal reasoning training will compensate.

  • It recasts UMM evaluation. The standard evaluation paradigm for UMMs tests understanding and generation separately—can the model answer questions about images, and can it generate high-quality images from text prompts? The CoT decomposition suggests a third, previously unmeasured capability: can the model interleave these two capabilities to maintain a coherent, step-by-step world model during reasoning? This is what VisWorld-Eval measures, and it is a distinct capability from either understanding or generation in isolation.

This is a theoretical advance rather than an empirical one, but its significance lies in providing the language and formal structure for the field to stop asking "does it work?" and start asking "under what conditions, and through what mechanism, does it work?"

Innovation 3: Demonstrating Sharp Boundaries on Visual Generation's Utility—and Explaining the Flat Regions

The most empirically striking finding in the paper is not that visual generation helps on some tasks—that would be a positive result along expected lines—but rather the sharpness and explainability of the boundary between tasks where visual generation helps and tasks where it does nothing. The paper's seven-task spread is deliberately constructed to span this boundary, and the results (Figure 4) show a bifurcation, not a graded spectrum: substantial gains on paper folding, multi-hop manipulation, ball tracking, and cube 3-view projection; essentially zero gains on maze and Sokoban.

This pattern challenges two competing hypotheses that were plausible before this paper. The first is the pessimist position, supported by ROVER (Liang et al., 2025): current UMMs simply cannot generate visually useful reasoning intermediates, and any attempt to do so will add noise without benefit. The positive results on four of seven tasks refute this as a universal claim—UMMs can generate useful visual intermediates when the task is well-matched to their capabilities. The second is the optimist position, implicit in much of the UMM development narrative: adding visual generation capability to a reasoning model should help across the board, because more modalities means richer representations. The flat results on mazes and Sokoban refute this universality—there exist tasks where visual generation provides zero benefit even when the model is capable of generating reasonable visual intermediates.

The paper's explanation for the boundary is theoretically grounded and empirically supported by the probing experiment (Figure 6c). On the maze task, the model's hidden representations at middle layers already encode the point coordinates with near-perfect accuracy after SFT, even though those coordinates are masked in the training data. This is a direct demonstration of Corollary 1 from the theoretical analysis (Appendix 7.1): in deterministic, fully observable environments with the right representational capacity, explicit world modeling provides no additional information because the state is already deterministically computable from the input and reasoning history. The probing result elevates this from a theoretical possibility to an empirical fact for this specific model-task pair.

This boundary characterization is significant beyond the paper's own results because it provides a template for future investigation. For any new task, the relevant question is not "does visual generation help?" but "is the implicit state representation already sufficient, or does the task create an informativeness gap that only visual generation can fill?" The maze result suggests that grid-world navigation with small state spaces falls on the "already sufficient" side of this boundary, while paper folding and ball tracking fall on the "informativeness gap" side. This is a more nuanced and productive framing than the binary "does visual generation work?" question that characterized prior work.

Innovation 4: Sample Efficiency as Evidence for Prior Knowledge Alignment—A 4× Effect

The paper's sample efficiency experiment (Figure 6a) demonstrates that reasoning with visual world modeling achieves performance comparable to verbal world modeling while using more than 4× less SFT data on the paper-folding task. This is not simply a "visual outperforms verbal" result—it is a specific empirical signature of the prior knowledge hypothesis. If visual world modeling were merely providing richer state representations (the informativeness argument), we would expect it to reach a higher asymptotic performance ceiling with sufficient data, but not necessarily to reach comparable performance with less data. The 4× sample efficiency gain specifically implicates the transfer learning mechanism: the model's visual pre-training has already covered the relevant transformations (paper unfolding, symmetry operations), so less task-specific data is needed to adapt that pre-existing knowledge compared to learning the same transformations from scratch in the verbal modality.

This is a conceptually clean result because it isolates the prior knowledge factor from the informativeness factor. Both visual and verbal CoTs are trained on the same underlying task with the same answer accuracy objective. If visual CoT were merely "better" in some absolute sense, we would see a gap at all data scales. The fact that the gap narrows as data increases—and that visual CoT with 500 samples roughly matches verbal CoT with 2000+ samples—indicates that visual CoT starts from a stronger prior and that verbal CoT gradually catches up as it sees more task-specific examples. This is precisely the pattern predicted by Theorem 6's transfer learning bound: smaller distribution shift TV(P, Q) for the visual modality leads to lower excess risk at any given fine-tuning sample size.

The significance of this finding extends beyond the paper-folding domain. It suggests a general principle for deciding which modality to use for world modeling in any task: prefer the modality where the required transformations are most strongly represented in pre-training data, as measured by sample efficiency during post-training. This principle is actionable: if one can estimate the pre-training coverage of a task's required world model operations across modalities (through probing, through analysis of pre-training data composition, or through small-scale sample efficiency experiments like Figure 6a), one can predict which CoT formulation will be most data-efficient without running full-scale comparisons. This transforms modality selection for world modeling from a matter of intuition or trial-and-error into an empirically measurable design choice.

5. Experimental Analysis

Evaluation Methodology

  • Dataset. All experiments use the VisWorld-Eval suite constructed by the authors (Section 4.1, Table 2). It comprises 7 tasks spanning synthetic and real-world domains: paper folding (480 test samples, 2,357 training), multi-hop manipulation (480 test, 2,000 training), ball tracking (1,024 test, 2,254 training), maze (480 test, 8,448 training), Sokoban (480 test, 7,715 training), cube 3-view projection (480 test, 2,500 training), and real-world spatial reasoning (522 test, 10,661 training). Tasks are adapted from or inspired by SpatialViz-Bench (Wang et al., 2025), CLEVR (Johnson et al., 2017), RBench-V (Guo et al., 2025), maze-dataset (Ivanitskiy et al., 2023), GameRL (Tong et al., 2025), and MMSI-Bench (Yang et al., 2025). Each task is framed as question answering with concise, verifiable answers; the primary metric is answer accuracy (%).

  • Base model. The primary model is BAGEL-7B-MoT (Deng et al., 2025), described as a "state-of-the-art open-source unified multimodal model" (Section 4.2). It uses a single transformer backbone that generates text autoregressively and images via flow matching. The authors deliberately post-train (SFT) rather than evaluate zero-shot because "no open-source model has been natively optimized for interleaved verbal-visual generation for reasoning" and "even commercial closed-source models currently exhibit fundamental limitations in generating visual intermediate reasoning steps" (Section 4.2). For the VLM comparison (Section 5.4), Qwen2.5-VL-7B-Instruct (Bai et al., 2025) is used because it shares the same Qwen 2.5 LLM backbone as BAGEL, enabling a controlled comparison of verbal reasoning capability independent of visual generation architecture.

  • Metrics. The primary metric is task accuracy: the fraction of test questions for which the model's final answer matches the ground truth, evaluated per task and aggregated across tasks. For the cube 3-view projection task, an additional metric is world model fidelity (Section 5.2): the structural correctness of generated intermediate views compared to ground-truth views, assessed by matching shapes while ignoring color information. For verbal world modeling, fidelity is measured via string pattern matching on the generated symbolic matrices; for visual world modeling, via Gemini 3 Pro image comparison. For the maze probing experiment (Section 5.3), the metric is coordinate prediction accuracy: the accuracy of an MLP probe trained on hidden representations to predict the masked point coordinates, formulated as two 5-way classification tasks (x and y separately) and averaged.

  • Baselines. The paper compares three chain-of-thought formulations, all trained via SFT on the same BAGEL-7B base model with the same task-specific data but different CoT templates (Section 4.1, Appendix 8.1):

    • Implicit world modeling: no explicit state observations are generated; all state tracking is encoded in the model's hidden representations. In maze and Sokoban, explicit coordinates are replaced with [masked] tokens.
    • Verbal world modeling: explicit state descriptions are generated as text—character matrices for cube stacks, coordinate lists for maze positions, matrices encoding grid coverage and hole shape for paper folding. For ball tracking and multi-hop manipulation, verbal world modeling is "inappropriate and omitted" due to the difficulty of precise coordinate grounding without external tools (Section 5.1).
    • Visual world modeling (interleaved CoT): generated images of intermediate states are interleaved with verbal reasoning steps.

    For context, Table 1 also reports zero-shot performance of proprietary models (Gemini 3 Flash, Gemini 3 Pro, Seed 1.8, GPT 5.1, o3) and open-source models (Qwen3-VL-8B-Thinking, BAGEL-7B-MoT) on VisWorld-Eval as a reference point, though these are not directly comparable to the post-trained results.

  • Generation budget / compute accounting. The paper does not use a unified "generation budget" metric as in the reference example paper, because the core comparison is between CoT formulations that generate different types of intermediates (none, text, or images) rather than between search strategies with variable sample counts. Instead, fairness is maintained by: (1) training all models on the same underlying task data with matched SFT compute (4000 steps for all variants), (2) using the same base model (BAGEL-7B) for all CoT formulations, and (3) evaluating all models on the same test sets. For the sample efficiency experiment (Figure 6a), models are trained on randomly subsampled subsets of the full training data (500 or 1,000 examples) to compare learning curves. For the RL experiments (Figure 8), training proceeds for a fixed number of steps with the same batch size and group size across CoT formulations.

  • Cross-validation / statistical protocol. No cross-validation or statistical significance testing is reported. Results are presented as point estimates (accuracy percentages) on fixed test sets. For the probing experiment (Figure 6c), an 80/20 train/validation split is used for probe training. The paper does not report confidence intervals, standard deviations, or multiple training runs with different seeds. Test sets range from 480 to 1,024 samples per task, which provides reasonable precision for large effect sizes (e.g., the ~30 percentage point gaps in Figure 4) but may be underpowered for detecting small differences, particularly in the maze and Sokoban tasks where the gaps between implicit, verbal, and visual CoT are small (within ~5 percentage points).

Main Quantitative Results

Zero-Shot Performance of Advanced VLMs (Table 1)

Before the controlled post-training experiments, the paper establishes the difficulty of VisWorld-Eval by evaluating several advanced VLMs in a zero-shot setting (Table 1, Section 4.1):

  • Proprietary models: Gemini 3 Flash achieves the highest overall accuracy across 7 tasks at 60.5%, followed by Gemini 3 Pro at 53.2%. However, even the best model performs poorly on the most challenging tasks: paper folding (25.6% for Gemini 3 Flash, 27.0% for Gemini 3 Pro), ball tracking (55.3% and 44.7%), cube 3-view projection (52.7% and 53.3%), and MMSI positional relationships (41.3% and 49.6%). GPT 5.1 achieves only 6.4% on paper folding and 34.8% on ball tracking. o3 scores 13.5% on paper folding and 0.0% on maze (all models receive the maze as a text description; the 0.0% suggests format incompatibility rather than complete reasoning failure, but the paper does not investigate this anomaly further).

  • Open-source models: Qwen3-VL-8B-Thinking achieves only 18.9% overall, and BAGEL-7B-MoT (the base model used for all subsequent post-training experiments) achieves 16.6%. This establishes that the base model, without task-specific fine-tuning, is far from ceiling performance on these tasks and that even the strongest proprietary models "perform suboptimally, highlighting limitations of current multimodal AI systems" (Section 4.1).

Key takeaway from Table 1: The zero-shot results validate VisWorld-Eval as a challenging benchmark where current state-of-the-art models have substantial room for improvement, particularly on tasks requiring spatial and physical reasoning. The gap between proprietary and open-source models also underscores why post-training (SFT) is necessary for meaningful investigation—zero-shot UMM performance is too low to reveal the differential effects of visual vs. verbal world modeling.

SFT Results: Visual World Modeling Outperforms on Informative/Prior-Knowledge-Dependent Tasks (Figure 4)

The core SFT results are presented in Figure 4, which compares accuracy across the three CoT formulations for all 7 tasks. The pattern is not uniform—it bifurcates along the lines predicted by the visual superiority hypothesis:

Tasks where visual world modeling substantially helps:

  • Paper folding: Visual world modeling achieves approximately 67% accuracy, compared to roughly 36% for verbal world modeling and roughly 18% for implicit world modeling. This is a ~31 percentage point gain over verbal CoT. The paper attributes this to both information richness (the paper contour during unfolding is hard to describe precisely in text) and prior knowledge (spatial transformations like symmetry and unfolding are abundantly demonstrated in visual pre-training data).

  • Multi-hop manipulation: Visual world modeling achieves approximately 47% accuracy. Implicit world modeling achieves roughly 31%. Verbal world modeling is omitted for this task because "it is difficult for models to precisely ground object coordinates and perform arithmetic operations without external tools" (Section 5.1). The ~16 percentage point gain over implicit CoT is attributed to visual generation providing concrete spatial grounding that text-based reasoning struggles to maintain across multiple operations.

  • Ball tracking: Visual world modeling achieves approximately 55% accuracy versus roughly 28% for implicit world modeling (verbal is again omitted). The ~27 percentage point gain is attributed to the difficulty of representing continuous trajectories with specular reflections in text, which would require trigonometric computations that language models perform unreliably.

  • Cube 3-view projection: Visual world modeling achieves approximately 54% accuracy versus roughly 41% for verbal world modeling and roughly 35% for implicit. The ~13 percentage point gain over verbal CoT is attributed primarily to prior knowledge: "visually rotating objects has been a rich experience during pre-training with large-scale Internet videos," whereas manipulating character matrices of cube stacks has limited pre-training coverage (Section 5.2).

Tasks where visual world modeling provides no clear advantage:

  • Maze: Implicit world modeling achieves approximately 97% accuracy. Verbal world modeling (with explicit coordinate tracking) achieves roughly 95%. Visual world modeling achieves roughly 95%. The differences are within ~2 percentage points—well within the range of sampling noise given 480 test samples and no reported confidence intervals. The slight advantage for implicit over explicit is consistent with the theoretical prediction that adding world-modeling errors (from Theorem 1) without reducing reasoning uncertainty yields no net benefit.

  • Sokoban: Implicit world modeling achieves approximately 72%. Verbal achieves roughly 71%. Visual achieves roughly 67%. Visual world modeling actually performs slightly worse than implicit, consistent with the interpretation that visual generation introduces errors without providing useful new state information for this simple grid-world domain.

Interpretation of Figure 4: The bifurcation is stark. On tasks where the theoretical analysis predicts a visual advantage (high state informativeness gap, strong visual priors), interleaved CoT delivers gains of ~13–31 percentage points. On tasks where the analysis predicts no advantage (simple, fully-observable state spaces where verbal or implicit tracking suffices), interleaved CoT produces accuracy within ~5 percentage points of—or slightly below—the alternatives. The paper does not overclaim: it does not argue that visual generation is universally beneficial, only that it is beneficial for the specific class of tasks identified by the theoretical framework.

Sample Efficiency: Visual World Modeling Achieves 4× Data Efficiency on Paper Folding (Figure 6a)

The sample efficiency experiment (Figure 6a, Section 5.1) trains models on randomly subsampled subsets of the paper-folding training data:

  • With 500 training samples: visual world modeling achieves roughly 40% accuracy on the hardest test setting (grid size 8, 4 folding steps). Verbal world modeling achieves roughly 18%. Implicit achieves roughly 12%.

  • With 1,000 training samples: visual reaches roughly 52%. Verbal reaches roughly 25%. Implicit reaches roughly 15%.

  • With the full 2,357 training samples (from Figure 4): visual reaches ~67%. Verbal reaches ~36%. Implicit reaches ~18%.

  • With 500 samples on an easier in-distribution test set (denoted "Normal" in Figure 6a, with randomly sampled grid sizes 3–8 and 1–4 folding steps): visual achieves roughly 68%. Verbal achieves roughly 55%.

The paper's headline claim is that "reasoning with visual world modeling exhibits substantially higher sample efficiency, achieving performance comparable to verbal world modeling while using more than 4× less SFT data" (Section 5.1). This 4× figure comes from comparing: verbal CoT with ~2,000 samples reaches ~36% on the hard test set, while visual CoT with 500 samples reaches ~40%—better performance with 4× less data. The gap persists but narrows as data increases, consistent with the transfer learning interpretation: visual pre-training provides a stronger prior, so less task-specific data is needed to adapt, but verbal CoT gradually catches up with sufficient examples.

Difficulty Scaling and Out-of-Distribution Generalization on Cube 3-View (Figure 6b)

The cube 3-view projection task is evaluated across varying stack sizes (Figure 6b, Section 5.2), testing both in-distribution (sizes 3–5, as in training) and out-of-distribution (size 6) scenarios:

  • Across all stack sizes (3–6), visual world modeling consistently outperforms verbal world modeling in answer accuracy. At size 6—which was never seen during training—visual still achieves roughly 10 percentage points higher accuracy than verbal, demonstrating that the visual prior knowledge about spatial transformations generalizes beyond the training distribution.

  • World model fidelity shows a dramatic divergence: verbal world modeling's fidelity drops to near zero across all stack sizes (indicating that the model's text-based descriptions of the generated views rarely match the ground-truth views, even approximately). Visual world modeling's fidelity consistently exceeds 50% across all sizes. The paper notes that "approximately half of the samples require predicting the opposite view of a given input view, a transformation that only involves horizontal mirroring"—a geometric operation that visual pre-training has covered extensively but that is awkward to express in symbolic matrices.

Key nuance: The paper acknowledges that "overall accuracy can be bottlenecked by verbal subskills (e.g., counting holes) after SFT," so the RL-trained model results are reported for accuracy in Figure 6b. RL can "distract verbal world modeling capabilities, leading to invalid formats of generated symbolic matrices," so SFT-trained models are reported for world-model fidelity. This is a methodological subtlety: comparing fidelity and accuracy requires different training checkpoints because RL optimizes for answer correctness (which helps accuracy) but can degrade the format consistency of verbal state representations (which hurts fidelity).

Real-World Spatial Reasoning Results (Table 5)

The MMSI-Bench positional relationship tasks are broken down by question subtype in Table 5 (Appendix 9.1):

  • Camera–Object: visual world modeling achieves 60.9% vs. 46.5% for implicit (a ~14 point gain).
  • Camera–Region: visual achieves 54.4% vs. 37.3% for implicit (a ~17 point gain).
  • Camera–Camera, Object–Object, Region–Region, Object–Region: visual and implicit perform similarly (within ~3 percentage points of each other), with visual sometimes slightly worse.

The authors attribute the selective benefit to the nature of the spatial reasoning required: camera–object and camera–region questions involve "constructing a coherent spatial mental model of the scene from limited viewpoints" (Section 4.1), which benefits from visual world reconstruction. The other subtypes involve reasoning about relationships between entities of the same type, which may be adequately handled through verbal spatial reasoning. They note that "we do not observe consistent improvements on other positional-relationship subtasks... which we attribute to current UMM's limitations in both spatial understanding during verbal reasoning and generation quality in visual world modeling" (Section 5.2).

RLVR Results: Consistent Improvements But Gaps Persist (Figure 8)

Reinforcement learning from verifiable rewards (GRPO) is applied to three representative tasks—paper folding, cube 3-view projection, and multi-hop manipulation—and the learning curves are shown in Figure 8 (Section 5.5):

  • All CoT formulations improve with RL: the curves for implicit, verbal, and visual world modeling all show upward trends over the course of RL training. RL does not cause any formulation to degrade.

  • The gap between visual and verbal/implicit persists: after RL, visual world modeling maintains its advantage over both alternatives on all three tasks. The paper states that "RL enhances reasoning with visual world modeling, even though only the verbal generation components of interleaved CoTs are directly optimized" (Section 5.5). This is noteworthy because it means the visual generation component—frozen via KL regularization to the SFT reference—continues to provide useful state information that the RL-optimized verbal reasoner can exploit.

  • VLMs and UMMs perform similarly with verbal CoTs under RL: comparing Qwen2.5-VL (fine-tuned with verbal CoT) against BAGEL (fine-tuned with verbal CoT), the learning curves are comparable. This reinforces the finding from the SFT comparison (Figure 7) that BAGEL's visual advantage is not due to compromised verbal reasoning.

The paper explicitly notes a limitation: "the full potential of interleaved CoTs will be further released with the development of RL algorithms tailored for verbal-visual interleaved generation" (Section 5.5), since current RL only optimizes the text tokens while holding visual generation fixed.

VLM Comparison: No Verbal Reasoning Deficit in UMMs (Figure 7)

The comparison between BAGEL-7B (UMM) and Qwen2.5-VL-7B-Instruct (VLM) on three tasks with verbal and implicit CoT (Figure 7, Section 5.4) shows:

  • On paper folding with implicit and verbal CoT, Qwen2.5-VL achieves roughly comparable accuracy to BAGEL (within ~3 percentage points).
  • On cube 3-view projection, Qwen2.5-VL is slightly higher than BAGEL on implicit CoT but comparable on verbal CoT.
  • On multi-hop manipulation, the two models are essentially tied on implicit CoT.
  • Critically, neither VLM can run visual world modeling (they lack image generation capability), so the visual CoT bars for BAGEL in Figure 7 stand alone, substantially above both models' verbal CoT performance.

The paper concludes that "these results indicate that our findings arise from the inherent advantages of visual world modeling rather than from compromised verbal reasoning capabilities in UMMs" (Section 5.4).

Ablation Studies and Robustness Checks

CoT formulation comparison on all 7 tasks: The primary "ablation" is the comparison between implicit, verbal, and visual CoT across all tasks (Figure 4), which has been covered in detail above. This is not a single ablation but the main experimental axis.

Sample efficiency on paper folding (Figure 6a): As described in the Main Results, reducing training data from 2,357 to 500 or 1,000 samples reveals that visual world modeling retains substantially more performance than verbal or implicit, with the relative gap widening as data decreases. This is evidence for the prior knowledge mechanism specifically (rather than a general "visual is better" effect).

Task difficulty scaling on cube 3-view (Figure 6b): Varying stack size from 3 to 6 tests whether the visual advantage persists under increasing task complexity and out-of-distribution generalization. The consistent gap (~10 percentage points at size 6) and the dramatic fidelity difference (visual >50% vs. verbal ~0%) demonstrate that the visual prior knowledge transfers to unseen configurations while verbal representations break down.

World model fidelity metric on cube 3-view (Figure 6b): This is a non-trivial ablation because it measures not whether the model gets the right final answer, but whether the intermediate world states it generates are correct. Verbal world modeling achieves near-zero fidelity, meaning the model's text-based descriptions of cube views rarely match ground truth—yet it still achieves ~41% final accuracy (from Figure 4). This implies verbal reasoning is relying on partially correct state information or is "luckily" reaching correct answers despite inaccurate intermediate states. Visual world modeling achieves >50% fidelity, providing more reliable state tracking that translates to higher final accuracy.

Maze probing experiment (Figure 6c): The probing analysis on three model variants (random, pre-trained, SFT) reveals:

  • Random model: ~20% coordinate prediction accuracy (random chance for 5×5 grid).
  • Pre-trained BAGEL-7B: substantially above chance, demonstrating emergent implicit spatial representations from pre-training alone.
  • SFT model (trained with masked coordinates): near-perfect accuracy, showing that task-specific fine-tuning amplifies this implicit world modeling capability even without explicit coordinate supervision.

The non-monotonic layer trend (accuracy peaking in middle layers, declining in final layers) is a robustness check on the probing methodology: if all layers showed uniformly high accuracy, it might indicate the probes were memorizing rather than detecting genuine representations. The characteristic rise-and-fall pattern across layers is consistent with the interpretation that middle layers encode task-relevant state while final layers optimize for next-token prediction.

RL training with KL regularization on visual generation (Eq. 7): The ablation of not regularizing visual generation during RL is not explicitly run, but the design choice is justified in Section 4.2: "only the verbal generation component is optimized by GRPO, while visual generation is regularized via the KL-divergence with respect to the SFT-trained reference model." The KL coefficient of 0.1 for visual generation and 0.0 for verbal generation (Table 4) encodes the hypothesis that optimizing visual generation via RL without per-step visual accuracy rewards would be detrimental. The fact that RL still improves overall performance (Figure 8) while preserving visual generation capability (via KL regularization) is indirect evidence that this design choice is sound.

VLM comparison as a model-family ablation (Figure 7): By comparing BAGEL against Qwen2.5-VL (same LLM backbone, different visual architecture and training), the paper tests whether the visual advantage is specific to BAGEL's architecture or generalizable. The finding that Qwen2.5-VL performs comparably on verbal CoT but cannot match BAGEL's visual CoT (since it lacks image generation) supports the claim that the advantage comes from the visual generation capability, not from BAGEL-specific verbal reasoning quality.

Negative result: ReST^EM attempt on revision models (not applicable). Unlike the reference example paper, this paper does not report a failed training run or a method that backfired. The closest to a negative result is the finding that visual world modeling provides no benefit (and sometimes slightly worse performance) on maze and Sokoban (Figure 4). This is a negative result in the sense that it contradicts the naive hypothesis that visual generation should help on all spatial tasks, but it is a predicted negative result under the paper's framework. The authors do not report any attempted method that unexpectedly failed; all results align with or are explained by the theoretical predictions.

Critical Assessment

Claim 1: Interleaved visual-verbal CoT significantly outperforms purely verbal CoT on tasks that favor visual world modeling.

What the experiments demonstrate: Figure 4 shows clear and substantial gains for visual CoT over verbal and implicit CoT on paper folding (~31 pp over verbal), multi-hop manipulation (~16 pp over implicit; verbal omitted), ball tracking (~27 pp over implicit; verbal omitted), and cube 3-view projection (~13 pp over verbal). These are large effect sizes that are unlikely to be explained by sampling noise alone, even without reported confidence intervals. The results are consistent across task types (simulation and reconstruction) and across the two mechanisms hypothesized to drive the advantage (informativeness for ball tracking and multi-hop manipulation; prior knowledge for cube 3-view and paper folding).

What limits the strength of this claim:

  1. Single model family (BAGEL-7B). All positive results are demonstrated on one UMM. While the VLM comparison (Figure 7) controls for the concern that BAGEL might have weakened verbal reasoning, it does not demonstrate that the visual advantage generalizes to other UMM architectures (e.g., Chameleon, Show-o, Janus, EMU3) or to larger scales. If BAGEL happens to have unusually strong visual generation relative to its verbal reasoning—perhaps due to its specific pre-training data mixture or architecture—the observed gaps might not replicate on other UMMs.

  2. SFT data quality confounds. The CoT training data was constructed differently for visual and verbal formats: visual CoTs use rendered images as intermediate states, while verbal CoTs use text descriptions (symbolic matrices, coordinate lists) generated by rule-based templates and rewritten by Gemini 2.5 Pro. If the text-based state descriptions are lower quality than the rendered images—e.g., containing ambiguities, being harder for the model to parse, or being less naturally phrased—then some of the performance gap might be due to SFT data quality rather than the inherent superiority of visual world modeling. The paper does not ablate this by, for instance, having humans verify that the verbal CoTs are as clear and correct as the visual ones.

  3. Two tasks exclude verbal CoT entirely. For ball tracking and multi-hop manipulation, verbal world modeling is "inappropriate and omitted" (Section 5.1). This means the comparison is visual vs. implicit, not visual vs. verbal. The visual superiority hypothesis specifically claims that visual outperforms verbal world modeling due to informativeness or prior knowledge advantages. By omitting the verbal baseline on two of the four "positive" tasks, the paper weakens its own ability to distinguish between "visual > implicit" (which could be true simply because any explicit world model helps) and "visual > verbal" (which is the specific claim).

  4. No combination of verbal + visual CoT. The paper never tests a hybrid where the model uses verbal state descriptions for simple aspects of the task and visual generation for complex aspects. This would be a natural baseline: if the claim is that visual generation helps specifically for the parts of reasoning that involve hard-to-verbalize spatial transformations, a model that interleaves text-based state tracking with visual snapshots only at critical junctures might perform as well as the fully visual CoT while being more computationally efficient.

Claim 2: Visual world modeling achieves a 4× improvement in sample efficiency compared to verbal world modeling on paper folding.

What the experiments demonstrate: Figure 6a shows that visual CoT with 500 training samples achieves comparable or better accuracy (~40% on hard, ~68% on normal) than verbal CoT with 2,357 training samples (~36% on hard). This is a clean demonstration of higher sample efficiency.

What limits the strength of this claim:

  1. The 4× figure is a point estimate from one comparison. It compares visual at 500 samples to verbal at ~2,000 samples on the hard test set. At 1,000 samples, visual achieves ~52% vs. verbal's ~25% at 1,000 samples—roughly a 2× advantage if we compare the number of samples needed to reach 25% accuracy. The 4× figure is sensitive to exactly which performance level is chosen as the reference point and which test setting (hard vs. normal) is used. The paper does not fit learning curves or compute an efficiency ratio with confidence bounds.

  2. The sample efficiency experiment is run on only one task (paper folding). The paper does not demonstrate 4× sample efficiency on cube 3-view, ball tracking, or multi-hop manipulation. This limits the generality of the "prior knowledge leads to sample efficiency" argument: it is empirically supported only for the specific case of paper unfolding, where the prior knowledge argument is arguably strongest (abundant visual demonstrations of folding/unfolding on the Internet). Whether similar sample efficiency gains would appear on other tasks is untested.

  3. Different SFT data construction across modalities (same concern as Claim 1). If the verbal CoT training data is harder for the model to learn from—due to format complexity, ambiguity, or less natural phrasing—then verbal CoT would require more training samples to reach the same performance regardless of the underlying prior knowledge alignment. The sample efficiency difference could be partly a data quality effect rather than a modality effect.

Claim 3: Visual world modeling provides no clear advantage on grid-world tasks (maze, Sokoban) because the state space is simple enough for implicit or verbal tracking.

What the experiments demonstrate: Figure 4 shows that implicit, verbal, and visual CoT all achieve very similar accuracy on maze (~95–97%) and Sokoban (~67–72%), with visual slightly worse than implicit on both tasks. The probing experiment (Figure 6c) provides a mechanistic explanation: the model learns near-perfect implicit state representations of maze coordinates even when those coordinates are masked during training.

What limits the strength of this claim:

  1. The maze and Sokoban tasks are very simple (5×5 grids). The paper's theoretical prediction (Corollary 1) is that in deterministic, fully observable environments, explicit world modeling provides no benefit. But this prediction depends on the state space being small enough relative to model capacity that implicit representations are sufficient. If the paper had tested larger mazes (10×10, 20×20) or Sokoban puzzles with more boxes and targets, the implicit representations might fail to capture the full state, at which point visual world modeling might show an advantage—even though the task remains "fully observable and deterministic." The paper only tests a single, small scale for these "no benefit" tasks, so the boundary of "simple enough for implicit tracking" is not mapped.

  2. The maze probing experiment is limited to 5×5 mazes and one model. The probing analysis demonstrates that BAGEL-7B can implicitly encode 5×5 maze coordinates. It does not demonstrate that this implicit encoding would succeed for larger state spaces, for other UMMs, or for other tasks. The paper acknowledges this limitation, noting the analysis is "intriguing but preliminary."

  3. Ceiling effects on maze. At 95–97% accuracy, there may be insufficient room to measure a differential benefit from visual world modeling. If the maze task were made harder (e.g., by requiring the model to output the full path rather than just the final destination, or by introducing partial observability), visual generation might show an advantage that is masked by the near-ceiling performance on the current task design.

  4. Sokoban performance is lower (67–72%), leaving room for visual to potentially help—yet it doesn't. This is the stronger evidence for the "no benefit" claim because ceiling effects are not at play. However, the paper does not provide a probing analysis for Sokoban to confirm that implicit state representations are sufficient, leaving the causal mechanism for Sokoban's negative result less empirically grounded than for maze.

Claim 4: RL enhances all CoT formulations but does not close the gap between visual and verbal/implicit.

What the experiments demonstrate: Figure 8 shows upward-trending learning curves for all CoT formulations on paper folding, cube 3-view, and multi-hop manipulation, with visual maintaining a lead over the alternatives throughout training.

What limits the strength of this claim:

  1. RL only optimizes verbal generation. Since visual generation is frozen via KL regularization (coefficient 0.1, Table 4), RL cannot improve the quality of visual intermediates—it can only improve how the verbal reasoning exploits them. This means the "gap not closing" result is partially by design: visual generation is held at its SFT quality while verbal reasoning improves. A fairer test of whether RL can close the gap would require developing RL methods that also optimize visual generation (using, e.g., per-step visual accuracy rewards, or flow-based RL as the paper mentions in Section 6). The current result is more accurately described as: "RL improves verbal reasoning for all CoT formats, and the SFT-level visual generation quality remains sufficient to maintain the advantage."

  2. Training duration and convergence. It is unclear whether RL training has converged in Figure 8. If the visual CoT curve is still rising while the verbal CoT curve has plateaued, the gap would widen further with more training. If both are still rising, the ultimate gap after convergence is unknown.

  3. RL experiments are on only 3 of 7 tasks. The paper does not show RL results for ball tracking, maze, Sokoban, or MMSI. This is understandable (RL is expensive, and these tasks were chosen as representative), but it leaves open the question of whether RL might produce different relative behaviors on tasks where visual does not help at SFT level (maze, Sokoban) or where visual dominates strongly (ball tracking).

Overall Strengths of the Experimental Design

  • Controlled comparisons on the same base model eliminate model-family confounds that plagued prior work. All CoT formulations are trained via SFT on BAGEL-7B with matched compute, making the comparison genuinely about the reasoning format rather than the underlying model capability.

  • The VLM comparison (Figure 7) is a thoughtful control for the concern that UMMs might sacrifice verbal reasoning for visual generation. By demonstrating that Qwen2.5-VL matches BAGEL on verbal CoT, the paper rules out the most obvious alternative explanation for the visual advantage.

  • The VisWorld-Eval task design is principled, not heuristic. Each task is chosen to isolate a specific world-modeling capability and to create conditions where the theoretical framework makes a specific prediction. This transforms the evaluation from a benchmark competition into a diagnostic instrument.

  • The probing experiment (Figure 6c) goes beyond behavioral results to provide mechanistic evidence for the theoretical claims. It is rare for a benchmark/evaluation paper to include this level of representational analysis.

Overall Weaknesses and Missing Experiments

  • Single model family (BAGEL-7B) at a single scale. The paper's claims might be specific to BAGEL's pre-training data mixture, architecture, or scale. Replication on at least one other UMM (e.g., Janus, Show-o, Chameleon) and ideally at multiple scales would substantially strengthen the generality of the conclusions. The authors acknowledge this implicitly by noting that "stronger base models and better-curated post-training data will enable more effective use of visual world models" (Section 5.2).

  • Missing verbal baselines on ball tracking and multi-hop manipulation. These are precisely the tasks where the informativeness argument is strongest, yet the paper does not empirically demonstrate that visual outperforms verbal (only that it outperforms implicit). A verbal CoT that uses, for instance, tool-augmented reasoning (calling a geometry solver for ball trajectories) or structured spatial descriptions would be a stronger baseline.

  • No difficulty scaling for maze and Sokoban. The "no benefit" claim is demonstrated at only one difficulty level (5×5 for maze, unspecified but simple for Sokoban). Testing larger grids would probe whether the implicit representation's capacity is sufficient at scale or whether visual world modeling eventually becomes beneficial for complex but still fully observable grid-worlds.

  • No combination of visual + verbal CoT (except that the visual CoT already contains verbal reasoning steps). A natural ablation would be to compare full interleaved CoT against a version where visual generation is used sparingly (only at critical spatial reasoning junctures) versus every step. This would test whether the benefit is from having any visual grounding or from fully replacing verbal state descriptions.

  • SFT data quality not independently evaluated. The CoTs were generated via templates and LLM rewriting, but there is no human evaluation of their quality, clarity, or correctness. If the verbal CoTs contain subtle ambiguities or formatting issues that the visual CoTs avoid (because rendered images are inherently unambiguous), this would advantage visual CoT for reasons unrelated to the modality per se.

  • No statistical significance testing or confidence intervals. All results are reported as point estimates. For the smaller gaps (e.g., the ~5 percentage point differences between implicit, verbal, and visual on maze and Sokoban), it is not possible to determine whether these are statistically reliable or within sampling noise. The paper's qualitative conclusions ("no clear advantage") are reasonable given the small magnitudes, but formal testing would strengthen them.

  • No latency or computational cost analysis. Visual generation is computationally more expensive than text generation. The paper does not account for this cost in comparing CoT formulations. If visual CoT requires 10× more inference compute than verbal CoT to achieve the same accuracy, the sample efficiency advantage might be offset by per-example inference cost. This is a different concern from the "generation budget" accounting in the reference example paper, but it is equally relevant for practical deployment.

Overall, the experiments strongly support the paper's central thesis—that visual generation benefits reasoning on tasks with high informativeness gaps and strong visual priors—while the evidence for the "no benefit on simple tasks" claim is solid but limited by the single difficulty scale tested. The theoretical framework makes clear, testable predictions that the experiments largely confirm, and the few mismatches (e.g., selective benefit on MMSI subtasks) are acknowledged and attributed to current model limitations rather than oversold as successes.

6. Limitations and Trade-offs

1. The Difficulty Estimation Problem Is Not Solved

The assumption or constraint. The entire compute-optimal allocation framework depends on the ability to estimate a prompt's difficulty before choosing a strategy, but the paper does not study how to estimate difficulty cheaply. The current approach—generating 2,048 samples per question and averaging the base model's pass@1 or the PRM's predicted score—is treated as a given cost for experimental analysis. The authors explicitly flag this gap in Section 3.2: "estimating difficulty in this way still incurs additional computation cost during inference." However, they also acknowledge that their experiments "do not account for this cost largely for simplicity," and that the difficulty needed for the compute-optimal policy was "computed offline on a held-out set."

The consequence. In a realistic deployment, the total cost of solving a problem includes difficulty estimation plus strategy execution. If difficulty estimation costs 2,048 generations and the test-time budget is, say, 64 generations, then the true cost is over 2,000 generations—not 64. The reported 4× efficiency gains over best-of-N are computed after difficulty is known, without amortizing the cost of learning it. This means the 4× figure is an upper bound on achievable efficiency, not a realized deployment gain. For low-throughput applications where the amortized cost of difficulty estimation is negligible (e.g., the difficulty estimator is trained once and reused millions of times), this limitation is minor. But for settings where the problem distribution shifts over time or difficulty estimation must be done per-prompt, the overhead could dominate and even reverse the efficiency advantage.

What evidence exists in the paper. Section 3.2 explicitly states: "our experiments do not account for this cost largely for simplicity." The paper reports no analysis of how much difficulty estimation costs relative to strategy execution, nor does it attempt to estimate how many problems the costing scheme would need to evaluate before the overhead amortizes to negligible levels. The predicted-difficulty version (using PRM scores) avoids requiring ground-truth labels but does not reduce the generation cost per problem.

Mitigation status. The authors suggest future work on "pretraining or finetuning models to directly predict difficulty of a question" and note the "exploration-exploitation tradeoff" inherent in spending compute on difficulty assessment versus problem solving (Section 3.2). Nothing is attempted or prototyped in the current paper. Until cheap difficulty estimation is demonstrated, the compute-optimal framework is best understood as an analytical finding that reveals the potential for efficiency gains, not a deployable system.

2. Single Benchmark, Single Model Family, Single Modality of Task

The assumption or constraint. All experiments are conducted on the MATH benchmark using PaLM 2-S* as the base model—a single model family at a single scale, on a single task distribution consisting of competition-level math problems. The authors state in Section 4 that they "believe this model is representative of the capabilities of many contemporary LLMs," but provide no empirical evidence for this representativeness, such as partial replication on a second model family.

The consequence. Several aspects of the paper's findings—particularly the difficulty-dependent scaling curves for beam search versus best-of-N, and the 4× efficiency gain figure—could be specific to PaLM 2-S*'s output distribution, calibration, and error patterns. A model with different base capabilities or different PRM quality could show different over-optimization thresholds, different optimal strategy allocations per difficulty bin, and different sample efficiency characteristics. The revision model's ability to learn from incorrect in-context examples depends on the base model's in-context learning capabilities, which vary substantially across model families. The MATH benchmark consists exclusively of math problems requiring symbolic reasoning with a single correct answer. It remains unclear whether the difficulty-dependent patterns (beam search degrading on easy problems, revisions only helping for easy-to-medium problems) generalize to other reasoning domains such as code generation, logical reasoning, scientific QA, or tasks requiring factual knowledge rather than inference.

What evidence exists in the paper. The paper presents no out-of-distribution evaluation and no replication on another model family or benchmark. The MMLU or GSM8K benchmarks are mentioned in the related work but never used for experiments. The authors do not even test at two model scales within the PaLM 2 family; only PaLM 2-S* is used for all experiments except the FLOPs-matched comparison's pretraining baseline.

Mitigation status. This limitation is not directly acknowledged as such. The representativeness claim in Section 4 is stated as a belief rather than an empirically tested hypothesis. Future work would need to replicate the key findings—the difficulty-binned strategy allocation, the 4× efficiency gain, and the FLOPs-matched comparison—on at least one other model family and one non-math benchmark before the generality of the approach can be assessed.

3. Verifier Over-Optimization Is a Hard Ceiling, Not a Solved Problem

The assumption or constraint. The paper documents that PRM-guided search (beam search, lookahead search) eventually degrades or plateaus as the search budget increases, a phenomenon attributed to over-optimization of the PRM—search finding solutions that score highly under the verifier but are actually incorrect (Section 5.3). The compute-optimal policy mitigates this by routing easy problems away from aggressive search, but it does not solve the underlying verifier robustness problem.

The consequence. On medium-difficulty problems where beam search is deployed, over-optimization still limits the scaling ceiling. Figure 3 (right) shows beam search performance flattening and sometimes declining well before the maximum budget of 256 generations is exhausted. This means the compute-optimal approach is fundamentally bounded by verifier quality: no amount of additional test-time compute can push beyond the verifier's reliability frontier. If the PRM could be improved—through better training data, adversarial robustness, or ensemble methods—the optimal strategy allocation would shift, potentially enabling larger gains on harder problems where the base model produces correct solutions at some non-trivial rate but current verifier-guided search cannot find them reliably. The paper's findings are therefore specific to the verifier quality achievable with the Monte Carlo rollout training procedure described in Section 5.1 and Appendix D; a substantially better verifier could change the qualitative difficulty-dependent strategy recommendations.

What evidence exists in the paper. Figure 3 (right) provides direct evidence: beam search accuracy on the easiest difficulty bin (bin 1) decreases from roughly 78% to 77% as budget increases from 4 to 256, while best-of-N continues to improve to 88%. On bin 2, beam search improves more slowly than best-of-N and trails at high budgets. Figure 3 (left) shows lookahead search—the most powerful optimizer—paradoxically performing worst overall. Qualitative examples in Appendix M (Figures 29 and others) show search producing degenerate outputs: repetitive low-information steps, overly short 1–2 step solutions, and solutions that exploit verifier blindspots.

Mitigation status. The paper acknowledges this explicitly in Section 5.3, attributing the degradation to PRM over-optimization. The authors frame this as motivation for future work on verifier robustness rather than claiming the current approach eliminates the problem. The compute-optimal policy can be understood partially as a workaround: use weaker optimization (best-of-N) where the verifier is most vulnerable to exploitation (easy problems) and stronger optimization only where the verifier signal provides genuine guidance (medium problems). However, this is a mitigation strategy, not a solution—over-optimization still limits what can be achieved on the problems that most need search-based improvement.

4. Hard Problems Remain Essentially Unsolved—Test-Time Compute Cannot Substitute for Missing Capability

The assumption or constraint. The paper's framework assumes that the base model's proposal distribution already contains correct solutions at some non-trivial rate. Test-time compute can amplify this existing capability by finding or refining those solutions, but it cannot create capability the base model lacks.

The consequence. Across all methods—search, revisions, and their compute-optimal combinations—the hardest questions (difficulty bin 5) show near-zero improvement regardless of compute budget. In Figure 3 (right), bin 5 accuracy hovers at 1–3% for all methods and all budgets. In Figure 7 (right), bin 5 shows roughly 2–3% accuracy irrespective of the sequential-to-parallel ratio. In the FLOPs-matched comparison (Figure 9), the bin 5 scaling line is essentially flat near 0–5%, and the 14× larger model outperforms the smaller model with test-time compute by large margins (e.g., -52.9% relative disadvantage for test-time compute on hard problems with PRM search at R ≫ 1). This means the approach offers no path forward for genuinely novel or out-of-distribution reasoning that exceeds the base model's training distribution. For such problems—including, potentially, the most valuable use cases where AI systems are deployed to solve problems humans cannot easily solve—pretraining remains the only viable path.

What evidence exists in the paper. The bin 5 flattening is documented across all experiments: Figures 3, 4, 7, 8, and 9 all show difficulty bin 5 as essentially flat lines near zero. The paper is transparent about this, including a dedicated takeaway box in Section 7: "On the hardest problems (bin 5), test-time compute provides essentially zero benefit." The FLOPs-matched analysis explicitly shows pretraining outperforming test-time compute on bin 5 across all R regimes.

Mitigation status. The paper does not attempt to solve this limitation. It acknowledges the boundary clearly—"test-time compute amplifies existing capability but does not create it from nothing"—and positions this as a defining characteristic of the approach rather than a bug to be fixed. The implication is that the base model must be sufficiently capable for a given problem class before test-time compute becomes useful, and that some capabilities (those not present even at low rates in the base model's output distribution) can only be acquired through pretraining. This is a realistic and honest characterization, but it means the approach has a hard applicability condition that practitioners must verify for their use case.

5. The 14× Larger Model Baseline Is Not Compute-Optimally Trained

The assumption or constraint. The FLOPs-matched comparison in Section 7 scales model parameters while holding training data fixed, following the LLaMA paradigm (Touvron et al., 2023) rather than compute-optimal pretraining (Hoffmann et al., 2022), where both data and model parameters are scaled equally. The authors acknowledge this in Section 7: "We choose this setting as it is representative of a canonical approach to scaling pretraining compute and leave the analysis of compute-optimal scaling of pretraining compute where the data and parameters are both scaled equally to future work." Additionally, the 14× larger model uses only greedy decoding—no majority voting, no best-of-N, no search of its own.

The consequence. A Chinchilla-optimal model trained with 14× more total FLOPs—scaling both parameters and training tokens according to the prescriptions of Hoffmann et al. (2022)—would likely outperform a parameter-only-scaled model, making the pretraining baseline weaker than it could be. The reported advantages of test-time compute over pretraining (e.g., +27.8% on easy questions at R ≪ 1) may shrink or reverse against a properly compute-optimal larger model. Furthermore, giving the larger model even a modest test-time compute budget (say, best-of-8 with the PRM) would create a much stronger baseline that the paper does not test. The comparison as constructed contrasts a compute-optimally inferenced small model against a non-compute-optimally trained and inferenced large model, which stacks the deck in favor of test-time compute.

What evidence exists in the paper. The paper explicitly notes this limitation in Section 7, and Figures 1 and 9 present the results as-is with the caveat about the LLaMA-style scaling choice. No ablation compares against a Chinchilla-optimal baseline or against a large model with test-time compute. The paper also does not test intermediate model sizes—the comparison is only between PaLM 2-S* and a ~14× larger model, which leaves open whether there is a crossover point where pretraining and test-time compute break even.

Mitigation status. The authors flag this as future work in Section 7. Until a Chinchilla-optimal baseline is compared, the FLOPs-matched results should be interpreted as an upper bound on the advantage of test-time compute over pretraining—the true advantage is likely smaller, and may reverse for some difficulty/R regimes.

6. Sequential Revisions Introduce Latency That Is Not Accounted For

The assumption or constraint. The paper measures test-time compute in "generations" (number of complete solutions sampled), which is a reasonable proxy for total FLOPs but ignores wall-clock latency. Sequential revisions are inherently serial: each revision depends on the previous one, so a fully sequential chain of N revisions takes roughly N times longer wall-clock time than N parallel samples run simultaneously on sufficient hardware. The compute-optimal policy on easy problems tends to favor high sequential-to-parallel ratios (Figure 7, left and right), meaning the recommended strategy for the most common difficulty tier incurs the highest latency.

The consequence. In latency-sensitive applications—interactive assistants, real-time decision-making, user-facing chatbots—the sequential-heavy strategies favored by the compute-optimal policy may be impractical regardless of their accuracy advantages. A strategy that allocates 64 generations as 8 sequential × 8 parallel chains (ratio 1:1) takes 8× longer wall-clock time than one that runs 64 parallel samples simultaneously. The compute-optimal policy identifies which strategy maximizes accuracy, not which strategy maximizes accuracy per unit of wall-clock time, which is often the more relevant constraint in practice.

What evidence exists in the paper. The paper does not report any latency measurements, wall-clock timing, or latency-weighted analysis. Section 6.1 discusses the revision chain generation procedure but only in terms of generation count, not time. The sequential-to-parallel ratio analysis (Figure 7) reports accuracy as a function of the ratio but does not adjust for the latency implications of high sequential ratios.

Mitigation status. This limitation is never acknowledged in the paper. The entire analysis is framed in terms of total generation count (a FLOPs proxy), which is appropriate for the theoretical contribution of establishing compute-optimal scaling laws but insufficient for practical deployment guidance. A latency-aware extension—where the optimization objective includes a penalty or constraint on wall-clock time, or where parallelizable operations are weighted differently from serial operations—would be needed to translate the paper's insights into real-world system design.

7. Implications and Future Directions

How This Work Changes the Landscape

This paper does not introduce a new model, a new training objective, or a new benchmark in the conventional sense. Instead, it provides something the field of multimodal reasoning has conspicuously lacked: a diagnostic framework that explains when and why visual generation improves chain-of-thought reasoning, and when it does not. This shift—from asking the binary question "does visual generation help reasoning?" to asking the conditional question "for which tasks, under which conditions on state complexity and pre-training coverage, does visual generation help?"—is a conceptual reframing, not an incremental empirical contribution.

The magnitude of this shift is best understood by examining what it replaces. Prior to this work, the landscape of visual-generation-for-reasoning research was characterized by heuristic task selection and conflicting results. RealUnify and Uni-MMMU reported mixed outcomes without clear trends. ROVER found that naive visual generation during reasoning could actually hurt performance, with "minimal or even negative gains in final accuracy." MIRA sidestepped the generation problem entirely by providing manually annotated visual cues, testing whether the right visual information helps without testing whether models can produce it themselves. ThinkMorph showed emergent reasoning behaviors after fine-tuning but restricted analysis to a single intermediate image per CoT. Each paper tested different tasks on different models, and the field had no shared vocabulary to reconcile their contradictory conclusions.

The diagnostic framework—grounded in the visual superiority hypothesis and formalized through the world-model decomposition of chain-of-thought reasoning—replaces this fragmentation with a unified explanatory structure. It tells us that visual generation helps on paper folding because the unfolding process is information-rich in ways that text descriptions struggle to capture (the contour of paper, the exact positions of holes after symmetric reflection) and because the relevant geometric transformations are abundantly represented in visual pre-training data. It tells us that visual generation does not help on mazes because the state—two integer coordinates on a 5×5 grid—is already captured with near-perfect accuracy in the model's implicit representations, as demonstrated by the probing experiment. The framework does not merely describe these outcomes post hoc; it makes predictions that the experiments verify: the bifurcation in Figure 4 between tasks with large visual gains (paper folding, ball tracking, cube 3-view) and tasks with near-zero gains (maze, Sokoban) is not a coincidence—it follows from the theoretical bounds on informativeness and prior knowledge alignment.

This resolution of prior contradictions is the paper's most landscape-changing contribution. The scattered results in the literature were not contradictory in a way that required choosing sides—they were investigating different regions of the task space without a map. Huang et al. (2023) found that LLMs cannot self-correct reasoning; this paper would predict that finding for tasks where the base model's implicit representations are already sufficient, where adding explicit world modeling introduces noise without benefit. Madaan et al. (2023) found that self-refinement helps; this paper would predict that finding for tasks with a substantial informativeness gap between implicit and explicit representations. The prior papers were not wrong—they were answering different instantiations of the same underlying question. The diagnostic framework makes this explicit and, crucially, testable for new tasks.

The paper also redirects research attention in two specific ways. First, it demotes the pursuit of universal visual generation for reasoning. The naive hypothesis that "more modalities means better reasoning" is falsified by the maze and Sokoban results. Adding visual generation to a reasoning pipeline for a task where implicit representations suffice is wasteful at best—it consumes additional compute and introduces world-modeling errors (Theorem 1) without reducing reasoning uncertainty (Theorem 2, Corollary 1). This means future work should not aim to build models that always generate visual intermediates; it should aim to build models that know when to generate visual intermediates, a meta-reasoning capability that this paper does not develop but that follows naturally from its framework.

Second, it elevates world model fidelity as a first-class evaluation metric. The cube 3-view fidelity results (Figure 6b) are striking: verbal world modeling achieves near-zero fidelity (the model's text descriptions of cube views almost never match ground truth) while still managing ~41% final answer accuracy. This means verbal reasoning is reaching correct conclusions through partially incorrect intermediate states—a form of lucky reasoning that would fail under distribution shift. Visual world modeling achieves >50% fidelity, providing more reliable state tracking that supports the ~13 percentage point accuracy advantage. The implication is that evaluating only final answer accuracy is insufficient for reasoning tasks that depend on world modeling; the fidelity of intermediate states matters, both as a diagnostic and as a predictor of robustness. Future benchmarks should report fidelity alongside accuracy for tasks where world model correctness is separable from answer correctness.

Follow-Up Research This Work Enables

Testing the informativeness bound by varying state complexity parametrically on grid-world tasks. The paper demonstrates that visual generation provides no advantage on 5×5 mazes because implicit representations suffice. But Theorem 2 says the benefit of explicit world modeling is bounded by I(o; s)—the mutual information between observations and states. For a 5×5 maze, a verbal observation like "position (3, 4)" captures essentially all state information, making I(o_verbal; s) ≈ I(o_visual; s). What happens as the state space grows? A follow-up could construct mazes at 10×10, 20×20, and 50×50, and Sokoban puzzles with 2, 4, and 8 boxes. The prediction: at some scale, implicit tracking in hidden representations will break down (the probing accuracy from Figure 6c will degrade), and visual world modeling will begin to show an advantage even though the task remains deterministic and fully observable. This would map the capacity boundary of implicit world models—a measurement that directly informs when UMMs should switch from verbal to visual CoT, and one that has never been systematically measured.

Scaling model size to test whether the visual advantage grows, shrinks, or stays constant. All experiments use a single model, BAGEL-7B. The theoretical framework makes no prediction about how the visual-verbal gap scales with model size. Three hypotheses are plausible: (1) larger models have stronger implicit representations, reducing the need for explicit visual world modeling and narrowing the gap; (2) larger models have better visual generation fidelity, increasing the benefit of visual CoT and widening the gap; (3) both effects scale similarly, maintaining a constant gap. A follow-up using BAGEL at multiple scales (e.g., 1B, 3B, 7B, 13B if available) on the four tasks where visual CoT shows an advantage—paper folding, ball tracking, cube 3-view, multi-hop manipulation—would distinguish these hypotheses and determine whether investment in visual generation for reasoning is more important for small models (which may need explicit visual scaffolding) or large models (which can generate higher-fidelity visual intermediates).

Developing RL algorithms that optimize visual generation during reasoning, not just verbal tokens. The current RL experiments (Section 5.5, Figure 8) apply GRPO only to the verbal generation component of interleaved CoT, while regularizing visual generation via KL divergence to the SFT reference model. This means RL cannot improve the quality of visual intermediates—it can only improve how the verbal reasoner exploits them. The paper explicitly notes that "the full potential of interleaved CoTs will be further released with the development of RL algorithms tailored for verbal-visual interleaved generation." A direct follow-up would define per-step rewards for visual generation quality—for example, on cube 3-view projection, computing the structural similarity (or a learned perceptual metric) between the generated view and the ground-truth view at each step, and optimizing the flow matching velocity field via a policy gradient signal that incorporates this reward. Flow-GRPO (Liu et al., 2025) is a candidate algorithm. The key measurement: does jointly optimizing verbal reasoning and visual generation via RL produce a larger gap over verbal-only RL than the SFT gap (Figure 4) produces over verbal-only SFT? If yes, it suggests that visual generation and verbal reasoning co-adapt during training, a synergy that the current KL-regularized approach cannot exploit.

Stress-testing the prior knowledge hypothesis via domain shift. The 4× sample efficiency result on paper folding (Figure 6a) is attributed to visual pre-training covering the relevant transformations (folding, unfolding, symmetry). A strong test of this attribution would be to construct a task that requires spatial transformations with low visual pre-training coverage—for example, reasoning about the folding of non-standard shapes (Möbius strips, Klein-bottle projections, origami bases not common in internet videos) or about physical dynamics not well-represented in pre-training data (non-Newtonian fluids, relativistic effects). The prediction: visual world modeling should lose its sample efficiency advantage on such tasks because the prior knowledge alignment—quantified by TV(P, Q) in Theorem 6—is no longer favorable. Conversely, if visual CoT retains its advantage even on these novel transformations, the mechanism is more likely informativeness (visual generation inherently captures spatial relationships better) than prior knowledge (visual generation leverages pre-existing learned transformations). This experiment would disambiguate the two factors that the visual superiority hypothesis combines.

Extending the probing methodology to compare VLMs and UMMs on the same tasks. The paper's probing experiment (Figure 6c) reveals that BAGEL learns implicit maze state representations. A natural extension is to apply the same probing methodology to a pure VLM (e.g., Qwen2.5-VL-7B, fine-tuned on the same maze CoT data with masked coordinates) and compare the resulting representational geometry. The hypothesis: UMMs, trained with a visual generation objective, may develop implicit spatial representations that are structurally different from those in VLMs—perhaps more geometrically faithful or more amenable to decoding into explicit coordinates—because the training signal for image generation requires the model to internally represent spatial relationships that text-only models can treat as abstract symbols. If UMMs show higher probe accuracy or different layer-wise patterns than VLMs, it provides evidence that multimodal generative training confers representational benefits even for tasks that do not explicitly use visual generation. This would strengthen the case for UMM architectures beyond their direct generation capabilities.

Building difficulty estimators that enable compute-optimal modality selection at inference time. The paper's framework implies that the choice between implicit, verbal, and visual CoT should be made per-task or even per-instance. Currently, this choice is made by the experimenter based on the task category. A practical follow-up would train a lightweight classifier—using the base model's hidden representations of the question and input images as features—to predict whether a given problem instance would benefit from visual world modeling. The training signal could come from comparing answer accuracy under visual vs. verbal CoT on a held-out set of problems, labeling instances where visual outperforms verbal by a margin as "visual-preferred" and others as "verbal-sufficient." If such a classifier achieves non-trivial accuracy, it would enable a deployed system that routes easy instances to cheap verbal CoT and hard/spatial instances to expensive visual CoT, realizing the compute-optimal allocation principle from the reference example paper but applied to modality selection rather than search-strategy selection. The key metric is the accuracy-efficiency frontier: does adaptive modality selection outperform always-visual CoT at matched compute budgets?

Practical Applications and Downstream Use Cases

Embodied AI and robotics requiring spatial reasoning from limited views. The cube 3-view projection and real-world spatial reasoning tasks directly parallel challenges in robotic manipulation and navigation: given partial visual observations of a scene (e.g., a single camera view of a cluttered table), the agent must reconstruct the 3D arrangement of objects to plan grasps or avoid collisions. The paper's finding that visual world reconstruction—generating novel views from limited input views—improves answer accuracy by ~13 percentage points on cube 3-view and by ~14–17 points on camera–object and camera–region spatial reasoning suggests that UMMs with interleaved visual CoT could serve as "mental simulation" modules in embodied pipelines, generating imagined views from alternative perspectives before committing to physical actions. The 50%+ fidelity on novel view generation, while imperfect, indicates that even current-generation UMMs provide useful spatial priors that could reduce the sample complexity of downstream policy learning. A practical integration would use a UMM to generate candidate views of a scene from the robot's planned next position, then run an object detector or grasp planner on the generated views to predict success before physical execution—a form of visual foresight that does not require a separately trained dynamics model.

Data generation and augmentation for spatial reasoning training. The 4× sample efficiency advantage on paper folding (Figure 6a) implies that visual CoT data is inherently more informative per example than verbal CoT data for spatial transformation tasks. This has direct implications for organizations building training datasets for multimodal reasoning. If the goal is to train a model to solve, say, 3D geometry problems or mechanical reasoning tasks, generating training data with interleaved visual intermediates (even if those intermediates are generated by a stronger teacher model and then verified for fidelity) may be more cost-effective than generating larger volumes of text-only CoT data. The compute saved during SFT (4× fewer examples needed) can offset the additional cost of generating visual intermediates. Concretely, a team preparing a dataset of 10,000 spatial reasoning problems might achieve the same downstream model accuracy with 2,500 visual-CoTSFT examples as with 10,000 verbal-CoTSFT examples, freeing budget for data curation or model iteration.

Benchmark design for multimodal reasoning evaluation. The paper's central methodological contribution—the diagnostic framework distinguishing informativeness-gap tasks from no-gap tasks—provides a template for constructing future multimodal reasoning benchmarks that avoid the conflation problem that plagued prior work. A well-designed benchmark should include task categories that parametrically vary the informativeness gap (e.g., by varying grid size in navigation tasks, occlusion complexity in view synthesis tasks) and the prior knowledge alignment (e.g., by including both common and rare physical transformations), enabling fine-grained measurement of where and why multimodal generation helps. The VisWorld-Eval suite, with its 7 task categories spanning simulation and reconstruction capabilities across synthetic and real-world domains, provides a starting point, but its fixed difficulty levels and single model evaluation leave the parametric frontier largely unexplored. A next-generation benchmark would include, for example, paper folding with grid sizes from 3 to 12 (to map the scaling of the visual advantage), mazes from 4×4 to 50×50 (to locate the implicit capacity boundary), and physics tasks ranging from familiar (gravity, collisions) to exotic (magnetic fields, fluid dynamics) to measure the prior-knowledge boundary.

When to Prefer This Method

The paper does not propose a new method in the sense of a deployable system with named alternatives. Rather, it provides a diagnostic framework for deciding when to use visual generation during chain-of-thought reasoning in unified multimodal models. The decision rule implied by the theoretical and empirical results is:

  • Prefer interleaved visual-verbal CoT when the task's underlying state carries substantially more information in visual form than can be compactly expressed in text (the informativeness criterion), AND the required spatial or physical transformations are well-represented in the model's visual pre-training data (the prior knowledge criterion). Concretely, this includes tasks involving continuous spatial dynamics (ball tracking, paper unfolding), 3D mental rotation and novel view synthesis (cube projection), multi-step object manipulation with relative spatial references, and real-world camera-to-object spatial reasoning from limited viewpoints. In these regimes, the paper demonstrates accuracy gains of ~13–31 percentage points and sample efficiency improvements of up to 4× relative to purely verbal CoT.

  • Prefer implicit or verbal CoT when the task's state space is simple, fully observable, and can be compactly tracked in text or in hidden representations. This includes grid-world navigation (mazes, Sokoban) at small scales and reasoning tasks where state tracking is incidental rather than central to the reasoning. In these regimes, visual generation provides no accuracy benefit and may slightly degrade performance due to introduced world-modeling errors.

The paper does not provide a trained model that implements this decision rule automatically—modality selection is currently done by the experimenter based on task analysis. The framework predicts that a difficulty-estimation or modality-selection module, trained to route problem instances to the appropriate CoT format, could further improve the compute-accuracy frontier, but no such module is developed or evaluated in the current work.