SpatialTree: How Spatial Abilities Branch Out in MLLMs

ArXiv: 2512.20617

🎯 Pitch

Fine-tuning a multimodal LLM on one basic spatial skill (like judging distance) can actively damage its other low-level perceptual abilities, yet these same foundational skills synergize powerfully to boost complex reasoning. To resolve this tension, the authors show that simply suppressing a model's urge to "think out loud" on perceptual tasks lets reinforcement learning improve the entire hierarchy without breaking fragile perception.

1. Executive Summary

This paper introduces SpatialTree, a cognitive-science-inspired hierarchy that organizes spatial abilities in multimodal LLMs into four levels—L1 Perception, L2 Mental Mapping, L3 Mental Simulation, and L4 Agentic Competence—and builds the first capability-centric benchmark evaluating 27 sub-abilities across mainstream MLLMs. Through systematic supervised fine-tuning, the authors uncover a striking transfer dynamic: individual L1 abilities exhibit negative intra-level transfer (e.g., fine-tuning on distance degrades motion and relation skills) but strong cross-level transfer to higher-level tasks, while jointly training multiple L1 abilities produces multi-ability synergy that exceeds the sum of individual contributions. The paper further identifies a fundamental tension between reasoning and perception during reinforcement learning—naïve RL that encourages extensive "thinking" improves complex reasoning but degrades intuitive perception—and proposes an auto-think strategy that suppresses unnecessary deliberation for perceptual tasks, enabling RL to improve performance across the entire hierarchy. Establishing that foundational perception acts as a prerequisite for agentic competence while remaining fragile to over-optimization, the framework provides proof-of-concept that spatial abilities in MLLMs follow structured, hierarchical transfer dynamics that demand differentiated training strategies rather than uniform scaling.

2. Context and Motivation

The Core Problem: Spatial Abilities in MLLMs Are Fragmented and Poorly Understood

The fundamental question this paper tackles is: do spatial abilities in multimodal LLMs have an underlying structure that governs how they emerge, interact, and transfer across levels of complexity? Despite rapid progress in MLLMs—from single-image understanding to video reasoning and embodied agent control—our understanding of spatial intelligence in these models remains superficial. The field knows that models struggle with certain spatial tasks and excel at others, but lacks a principled framework for understanding why or how these abilities relate to one another.

This gap is significant for several practical and theoretical reasons:

Training efficiency: If spatial abilities have hierarchical dependencies—where higher-level skills build on foundational ones—then training can be strategically sequenced rather than uniformly applied. Without understanding this structure, practitioners waste compute on ineffective data mixtures or training strategies that inadvertently damage existing capabilities.
Capability diagnosis: When an MLLM fails at a complex spatial reasoning task, is the bottleneck truly in reasoning, or does it stem from a deficit in basic perception that went undiagnosed? Current benchmarks cannot answer this question because they evaluate tasks in isolation, treating each as an independent capability rather than nodes in a dependency network.
Safe deployment of spatial agents: As MLLMs increasingly control robots, navigate environments, and interact with physical objects, understanding the reliability and failure modes of their spatial cognition becomes safety-critical. A model that excels at causal reasoning about dynamics but has brittle distance estimation could make catastrophically wrong physical predictions—yet no existing evaluation framework would flag this vulnerability.
Cognitive science validation: Cognitive psychology has long theorized that spatial intelligence develops hierarchically in humans, progressing from sensorimotor perception to mental mapping to abstract reasoning and planning. Whether MLLMs exhibit analogous developmental structure is an open question with implications both for AI architecture design and for using these models as computational models of cognition.

The Fragmentation of Spatial Benchmarks

The paper identifies a clear pattern in how spatial evaluation has evolved: task-centric rather than capability-centric. This distinction is crucial and worth unpacking.

Early benchmarks, such as BLINK, SpatialEval, and 3DSR-Bench, evaluated spatial understanding in single images—tasks like relative object positioning, distance estimation, and spatial caption generation. Each benchmark defined its own task taxonomy, making cross-benchmark comparisons nearly impossible. As MLLMs advanced to handle multi-frame and video inputs, new benchmarks emerged to fill the resulting evaluation gaps: VSI-Bench for spatial reasoning across multiple views, MMSI-Bench for multi-image spatial intelligence, Omnispatial for comprehensive spatial reasoning, and SITE for dynamic reasoning tasks. More recently, EmbodiedBench and IR3D-Bench extended evaluation to agentic tasks and inverse rendering.

The result, as the authors describe in Section 1, is that spatial benchmarks remain "fragmented and often treat spatial capabilities as isolated or overlapping skills." The same underlying ability—say, distance estimation—might be tested in five different benchmarks under five different task formulations (multiple-choice depth ordering, numeric depth prediction, relative distance comparison, 3D coordinate estimation, and depth-grounded navigation), with no way to track whether a model's performance across these variants reflects a single coherent capability or five independent learned behaviors.

This fragmentation has concrete consequences:

No common vocabulary: Different benchmarks use different names for the same underlying ability. What one calls "spatial relation reasoning," another calls "object configuration understanding." There is no shared taxonomy that would allow researchers to aggregate findings across studies.
Difficulty confounding: Without controlling for the cognitive demands of individual tasks, it is impossible to tell whether a model's poor performance on a benchmark reflects genuine capability gaps or simply harder task formulations. A model might score 40% on Benchmark A and 60% on Benchmark B, but is this because the model is better at B's content or because B's questions are easier?
Transfer blindness: If two tasks share underlying requirements (e.g., both need distance perception), training on one should improve the other. But since benchmarks don't annotate these shared prerequisites, such transfer effects remain invisible. The field cannot systematically study which abilities support which others.
Coverage gaps: Task-centric benchmark design means capabilities that don't naturally fit into existing task formats get overlooked. The paper explicitly notes that agentic interaction (L4) was "largely absent from prior benchmarks" (Section 1) because it requires interactive evaluation rather than static question-answering. Similarly, orientation estimation—sensing gravity direction and object poses—was under-explored despite being a fundamental perceptual ability.

Prior Approaches and Their Limitations

The paper identifies several categories of prior work and their specific shortcomings:

Task-centric benchmarks (the status quo). As described above, these evaluate spatial abilities through specific task formulations without a unifying capability model. They are useful for tracking progress on individual tasks but cannot reveal the structure of spatial intelligence or guide systematic improvement.

Cognitive science theories of spatial intelligence. Classical work by Piaget, Tolman, and Kuipers established that human spatial cognition is hierarchical—progressing from sensorimotor perception to cognitive mapping to abstract reasoning. These theories provide rich conceptual frameworks but were developed for human cognition, not machine learning models. They offer no guidance on how to instantiate the hierarchy in benchmark design, what evaluation metrics to use for each level, or how to measure transfer between levels in an MLLM context. The paper positions SpatialTree as bridging this gap: drawing on cognitive science for the conceptual structure while building practical evaluation and training methodology for MLLMs.

Individual capability studies. Several recent efforts have explored specific spatial abilities in isolation. VST (Visual Spatial Tuning) investigated whether targeted fine-tuning on spatial data could improve spatial reasoning, finding some positive effects but not systematically studying transfer dynamics. CameraBench studied camera motion understanding, MMSI-Bench covered multi-image tasks, and IR3D-Bench evaluated inverse rendering as a form of spatial reasoning. Each of these provides valuable data points but operates within a narrow capability slice, making it impossible to study dependencies.

Low-level perception in MLLMs. The paper explicitly acknowledges BLINK's finding that "multimodal large language models can see but not perceive"—they can process visual inputs and produce plausible language outputs, but their raw perceptual judgments (distance, size, spatial relations) are surprisingly unreliable. This finding is a key motivator: if perception is fragile, then any higher-level ability built on top of it inherits that fragility, but no prior work had traced these dependency chains systematically.

How This Paper Positions Itself

The paper's central move is captured in its own framing question (Section 1):

"Can we move beyond disjointed, task-centric evaluations to uncover a compact set of atomic capabilities that reveal how spatial abilities emerge, interact, and transfer?"

This positions SpatialTree not as another benchmark competing with existing ones, but as a meta-framework that subsumes and reorganizes them. Rather than proposing new tasks, the paper proposes a new way of categorizing tasks—by underlying cognitive function rather than by surface task format. This is analogous to how the field of natural language processing moved from task-specific benchmarks (sentiment analysis, named entity recognition, question answering) to capability-based frameworks (understanding, generation, reasoning), though the paper does not make this analogy explicitly.

The key methodological innovations that enable this positioning:

Capability-centric taxonomy building. The authors derive their four-level hierarchy from cognitive science principles, specifically Piaget's insight that "intelligence is a dynamic structure built through successive stages." Each level is defined by what cognitive function it serves, not what task format it uses:

L1 Perception: raw spatial sensing, pre-linguistic
L2 Mental Mapping: linking spatial primitives to language and memory
L3 Mental Simulation: internal reasoning and planning about space
L4 Agentic Competence: executing actions in space

This taxonomy provides a common vocabulary that existing benchmarks lacked. A distance estimation task from SpatialEval and a depth comparison task from BLINK both map to L1.Geometry.Distance, regardless of their surface format differences.

Unified data engine. Rather than treating each benchmark's data as siloed, the paper builds a data curation pipeline (Section 4.1, Figure 3) that integrates existing datasets into the SpatialTree framework while filling coverage gaps with new annotations. This is practical bridge-building: the paper acknowledges the value of prior work's data collection efforts while providing the organizational structure those efforts lacked.

Causal intervention methodology. Perhaps most distinctively, the paper goes beyond static evaluation to directly test the hierarchical structure through targeted training interventions. The logic is: if the taxonomy is correct about which abilities are foundational and which are composite, then training on foundational abilities should produce measurable transfer to higher-level abilities, while the reverse should not hold. This transforms the taxonomy from a descriptive convenience into a falsifiable hypothesis about model capabilities. The SFT experiments in Section 6.1 and the RL experiments in Section 6.2 are direct tests of the hierarchy's validity.

Differentiated training as a design principle. The paper's positioning on training strategy is that spatial abilities require differentiated treatment—a departure from the prevailing "one-size-fits-all" approach where the same SFT or RL recipe is applied uniformly across all task types. The auto-think strategy (Section 6.2) operationalizes this: suppress reasoning for perceptual tasks where overthinking degrades intuitive judgments, encourage it for complex planning where deliberate computation is necessary. This is a concrete proposal for how understanding hierarchical structure should change training practice.

The Specific Gap This Paper Fills

To be precise about what was missing before this work:

No shared taxonomy for spatial abilities in MLLMs. Researchers could not say whether Model A's strength in "spatial reasoning" was the same thing as Model B's strength in "spatial understanding" because there was no common definition of what these terms meant or how they related to one another.
No systematic study of cross-ability transfer. The field knew that MLLMs could be fine-tuned to improve specific spatial skills, but had no evidence about whether improvements in one skill transferred to others—and if so, in which direction and under what conditions.
No principled approach to training spatial abilities holistically. Without understanding dependencies, training strategies were necessarily heuristic: throw diverse spatial data at the model and hope for the best. This paper provides the first evidence that such uniform strategies are suboptimal because different levels of the hierarchy respond differently to different training signals (reasoning-heavy vs. perception-direct).
No integration of agentic competence into spatial evaluation. Prior work treated spatial reasoning and embodied action as separate research threads. By including L4 Agentic Competence as the top level of the hierarchy—the culmination of perception, mapping, and simulation—the paper argues that they are not separate but integrally connected, and provides the first benchmark that evaluates them as such.

3. Technical Approach

3.1 Reader Orientation

SpatialTree is not a single model or training recipe but rather a capability-centric framework—a taxonomy, a benchmark, and a set of intervention methodologies—that together reveal how spatial abilities are structured in multimodal LLMs. The system solves the problem of fragmented, task-centric evaluation by organizing 27 spatial sub-abilities into a four-level cognitive hierarchy and then using targeted supervised fine-tuning and reinforcement learning experiments to validate that this hierarchy reflects genuine dependency and transfer relationships in the models. The "shape" of the solution is a cognitive-science-grounded tree structure (L1 → L2 → L3 → L4) paired with a data engine that populates each node with evaluation data, followed by causal training interventions that test whether lower-level abilities function as prerequisites for higher-level ones.

3.2 Big-Picture Architecture (Diagram in Words)

The SpatialTree framework has five major components:

The SpatialTree Taxonomy (Section 3): A four-level capability hierarchy (L1 Perception, L2 Mental Mapping, L3 Mental Simulation, L4 Agentic Competence) derived from cognitive science. Each level decomposes into sub-abilities (e.g., L1 into Geometry, Motion, Relation, Localization, Orientation) that define what is measured, not how it is measured.
SpatialTree-Bench (Section 4): The instantiated evaluation benchmark, built by (a) reorganizing existing task-centric datasets and mapping each question to a node in the taxonomy, (b) filling coverage gaps with SpatialPlus, a newly annotated dataset, and (c) designing level-appropriate evaluation metrics (multiple-choice, numeric accuracy, LLM-as-a-Judge, agentic execution scores).
The Spatial Data Engine (Section 4.1, Figure 3): A multi-tier pipeline of expert perception models, reconstruction systems, LLM-based rephrasers, and human annotators that process raw images and videos into evaluation questions and training data, organized hierarchically to match the taxonomy levels.
SFT Intervention Framework (Section 6.1): A methodology for causally probing transfer dynamics: fine-tune a base model on ability-specific data (e.g., L1 distance estimation) and measure the resulting performance changes across all other abilities in the tree, quantifying both intra-level and cross-level transfer.
Hierarchy-Aware RL Framework (Section 6.2): A training strategy that applies differentiated reinforcement learning signals per taxonomy level: suppressing reasoning rewards and adding length penalties for intuitive perceptual tasks (L1), while amplifying explicit chain-of-thought rewards for complex reasoning tasks (L3-L4).

Information flows as follows: raw visual data → Spatial Data Engine → taxonomy-organized evaluation questions and training data → baseline evaluation on untuned models → targeted SFT on selected abilities → re-evaluation to measure transfer → hierarchy-aware RL with level-specific reward shaping → final evaluation to validate the differentiated training approach.

3.3 Roadmap for the Deep Dive

First, the formal structure of the SpatialTree taxonomy (Section 3), because it defines the capabilities that everything else—evaluation, training, transfer analysis—organizes around. Understanding what each level measures and how levels relate conceptually is prerequisite to understanding the benchmark and experiments.
Second, the instantiation of the benchmark (Section 4), covering data curation (how existing datasets are reorganized and gaps filled), the Spatial Data Engine's architecture, and evaluation metric design. This explains how the abstract taxonomy becomes concrete measurement.
Third, the SFT methodology (Section 6.1), including the general data mixture recipe, the construction of targeted training data for specific L1 abilities, and the cross-ability measurement protocol that reveals transfer dynamics.
Fourth, the RL methodology (Section 6.2), covering the GRPO optimization, the hierarchy-aware reward mechanism (auto-think), and the experimental controls that ensure measured improvements are genuine capability gains rather than dataset memorization.
Fifth, the formal agentic model (Section 3.4), which defines the sequential decision-making formulation that underlies L4 evaluation, including the state-action-memory triplet and how MLLMs interface with environments through language.

3.4 Detailed, Sentence-Based Technical Breakdown

This is primarily a framework and empirical analysis paper whose core idea is that spatial abilities in MLLMs follow a hierarchical dependency structure that can be revealed through capability-centric evaluation and validated through targeted training interventions. The technical contributions span taxonomy design, benchmark construction, and training methodology.

The SpatialTree Taxonomy: Formal Capability Definitions

The taxonomy is the foundation of the entire framework. It defines four levels of spatial ability, each characterized by the cognitive function it serves rather than the tasks that exercise it. The levels are hierarchical in the specific sense that each builds on capabilities from the levels below it.

Level 1: Perception (L1). This is defined as the most primitive capacity to sense visual signals from the environment, corresponding to the sensorimotor stage in human cognitive development. The authors explicitly note that L1 operates "without relying on language or symbolic reasoning" (Section 3.1)—it is pre-linguistic spatial sensing. L1 decomposes into five sub-abilities:

Geometry: Interpreting physical form and metric properties. This includes Distance (gauging metric and relative depth), Size (estimating physical magnitude, area, and volume), and Shape (discerning contours, boundaries, and geometric primitives). The authors frame these evolutionarily: these faculties enable immediate judgments like "whether a fruit is small enough to hold or a path is wide enough to traverse."
Motion: Processing dynamic visual signals over time. Split into Egocentric (sensing self-motion and heading direction) and Allocentric (perceiving the movement and speed of external objects). This distinction matters because the two types of motion perception rely on fundamentally different visual cues—optic flow patterns for self-motion versus object tracking for external motion.
Orientation: Sensing spatial alignment relative to the environment. Includes Gravity (sensing the vertical axis) and Object orientation (perceiving poses). The gravity component is particularly notable because it is a physical invariant that humans sense via vestibular cues, but MLLMs must infer from visual patterns alone—the benchmark tests whether they can.
Relation: Registering how entities are spatially arranged. Includes Topology (inside, outside, overlap, occlusion) and Correspondence (recognizing the same object or landmark across different viewpoints). Correspondence is fundamentally about visual feature matching across viewpoint changes, making it a bridge between pure perception and the multi-view integration needed at higher levels.
Localization: Anchoring stimuli in 2D/3D space. Includes Detection (identifying object presence and spatial extent) and Grounding (associating observations with spatial positions or coordinates). This category addresses what the authors call "the fundamental question of where."

A critical design choice: L1 abilities are defined at the level of raw spatial sensing—they are about what the model can directly extract from visual input, not what it can reason about or describe in language.

Level 2: Mental Mapping (L2). This level marks a qualitative shift: it maps spatial perception to language and constructs language-structured spatial memory. The authors define two sub-abilities:

Understanding: Interpreting the semantic meaning of geometric perception. This includes Spatial Captioning (translating visual scenes into linguistic descriptions), semantic Relations (distinguishing "riding" from "sitting on"), semantic Motion interpretation (recognizing purposeful actions rather than simple movement), Perspective Taking (mentally aligning with alternative viewpoints), and Affordance understanding (identifying functional possibilities of objects, such as recognizing a handle as graspable). Affordance is particularly important because it bridges perception with potential future interactions—it is forward-looking in a way that pure captioning is not.
Memory: Extending spatial awareness beyond the instantaneous field of view. This relies on Cognitive Map construction (synthesizing fragmentary observations from video frames or multi-view images into a unified global representation) and Memory Retrieval (grounding specific semantic events or moments, such as recalling where an object appeared even when currently occluded). The cognitive map concept is drawn directly from Tolman's classical work on spatial representation.

The key insight of L2 is that it transforms raw spatial data into semantically meaningful representations that can be stored, queried, and reasoned about linguistically.

Level 3: Mental Simulation (L3). This level supports internal reasoning about space before action execution, aligning with the chain-of-thought paradigm. Two orthogonal sub-abilities:

Causal Reasoning: Modeling spatial interactions, physical dynamics, and entity relationships within a simulated mental space. Includes reasoning about object geometry (e.g., how shapes interlock in spatial puzzles), motion prediction (e.g., how an object traverses a path), and analyzing semantic-spatial relations (e.g., "object A is left of object B"). The key distinction from L1 and L2 is that L3 requires chaining multiple inferences—not just perceiving or describing, but predicting and explaining.
Sequential Planning: Converting causal insights into goal-directed action plans expressed in language. Includes designing step-by-step strategies (e.g., "first move toward the door, then turn right, finally interact with the handle") and generating abstract routes that respect spatial logic (e.g., "go around the table to reach the sofa"). The plans are linguistic action primitives—the output is language, not execution commands.

The orthogonal relationship between causal reasoning and sequential planning is important: reasoning is about understanding what will happen and why, while planning is about deciding what to do. They are complementary but separable cognitive functions.

Level 4: Agentic Competence (L4). This is the culmination, where internal plans translate into tangible interactions. The authors define L4 through a formal sequential decision-making model:

$(S_t, A_t, M_t) \sim P_\theta\left(\cdot \mid O_t, H_{t-1}\right)$

where the history is:

$H_{t-1} = \{(O_0, A_0, M_0), \ldots, (O_{t-1}, A_{t-1}, M_{t-1})\}$

and $O_t \in \mathcal{O}$ is the current multi-modal observation (the visual input at time $t$ ), $S_t \in \mathcal{S}$ is the internal latent state (goals, plans, or beliefs), $A_t \in \mathcal{A}$ is the chosen action, $M_t \in \mathcal{M}$ is the updated memory representation, and $P_\theta$ is the MLLM policy parameterized by $\theta$ .

What it computes: At each time step, given the current observation and the full history of previous observation-action-memory tuples, the model outputs a new state estimate, an action to execute, and an updated memory. This is a fully general formulation of an interactive spatial agent: it perceives, remembers, decides, and acts in a loop.

Why this form: This formalization explicitly distinguishes MLLM-based spatial agents from Vision-Language Action Models (VLAs) that decode low-level control signals. The authors note that "MLLMs take the language as the only interface to link with environments like GUI Agents." This means the action space must be designed to be expressible in language (discrete action primitives with natural language descriptions) rather than continuous motor commands. The memory component $M_t$ is crucial because spatial tasks require maintaining state across multiple observations—an agent navigating a room must remember what it saw behind it even when facing forward.

The L4 evaluation covers three embodiments: character navigation (game environments), robotic grippers (manipulation), and human hands (dexterous interaction). The action space is designed to be unified across these embodiments through the spatial action mapping system described below.

Benchmark Instantiation: From Taxonomy to Measurable Tasks

The SpatialTree-Bench is constructed through a systematic data curation pipeline that operates at four levels, each with its own data engine (Section 4.1, Figure 3).

Data Reorganization Principle. Rather than creating entirely new tasks, the paper maps existing benchmark questions to the SpatialTree taxonomy. Datasets including Omnispatial, MMSI-Bench, CameraBench, SpatialEval, 3DSR-Bench, VSI-Bench, SpatialViz-Bench, IR3D-Bench, EmbodiedBench, LLaVA-3D, and Multi-SpatialMLLM are reorganized. The mapping is based on what cognitive function each question exercises, not what surface format it uses. For instance, a multiple-choice question about object depth ordering from SpatialEval and a numeric depth estimation question from BLINK both map to L1.Geometry.Distance, even though their formats differ.

SpatialPlus: Filling Coverage Gaps. The paper identifies two major gaps in existing benchmarks: L1 Orientation (gravity estimation and object pose) and L4 Agentic Competence. For orientation, the authors annotate 500 images from TartanAir (drone footage) using GeoCalib for gravity estimation and Co3dv2 (object-centric images) using OrientAnything for object poses. For L4, they curate agentic data from game videos (Miradata), egocentric manipulation videos (EgoDex), and robot manipulation data (Droid), processed through the spatial action mapping pipeline.

L1 Data Engine (Perception). This engine operates at the lowest level of visual processing. It employs a suite of expert perception models to extract intermediate representations:

DepthAnything V3: Produces dense depth maps from single images, enabling distance and size estimation QAs without requiring ground-truth depth sensors.
SpatialTracker and SpatialTrackerV2: Perform 2D-to-3D point tracking across video frames, producing dense correspondence fields that enable correspondence-based QAs (e.g., "where does this pixel go in the other image?").
GeoCalib: Estimates camera parameters including focal length and gravity direction from single images, enabling orientation estimation QAs.
OrientAnything: Estimates 3D object orientation from single images, decomposing into azimuth, polar, and rotation angles.

The workflow is: expert models process raw images/videos → their outputs (depth maps, correspondence fields, gravity vectors, orientation angles) are converted into QA pairs using designed templates → LLMs rephrase the templates to improve linguistic diversity and naturalness. The rephrasing step is critical: it prevents models from overfitting to specific template patterns while preserving the underlying spatial reasoning requirement.

L2 Data Engine (Mental Mapping). For cognitive mapping and memory retrieval, the engine uses 3D reconstruction pipelines (described in Appendix C.2) to generate Bird's-Eye-View (BEV) maps from videos. These BEV maps are captioned using multimodal LLMs, then transformed into QAs that test whether the model can synthesize multi-frame observations into a unified spatial representation. For other L2 abilities (affordance, perspective taking, semantic relations), the engine builds on partially annotated datasets and augments them by "randomly constructing multiple-choice candidates through various visual prompts" and "reformulating questions with more abstract descriptions."

L3 Data Engine (Mental Simulation). For reasoning tasks, the engine takes existing annotated reasoning QAs (from CameraBench, MMSI-Bench, and others) and enriches them with explicit Chain-of-Thought reasoning through structured thinking templates. An LLM-based rephraser converts these templates into natural CoT-formatted QAs, producing the hybrid multi-option + LLM-as-a-Judge format used for evaluation.

L4 Data Engine (Agentic Competence). This is the most complex engine because agentic data requires executable action sequences, not just static QAs. The pipeline involves:

Action-Extraction Pipeline (Appendix C.2): Raw video data from game footage, egocentric manipulation, and robot datasets is processed to extract metric camera trajectories (navigation) or end-effector trajectories (manipulation). For navigation, the engine reconstructs Camera-to-World transformation matrices and decomposes continuous camera motion into discrete action primitives. For manipulation, the engine extracts 7-DoF end-effector poses and gripper states.
Spatial Action Mapping (Table A in Appendix C.2): A unified action space that maps diverse embodiment-specific controls into a common set of motion primitives with natural language descriptions:
- Translation primitives: Truck (left/right, mapped to A/D keys), Dolly (forward/backward, W/S), Pedestal (up/down, Q/E)
- Rotation primitives: Pan (yaw left/right, arrow keys), Tilt (pitch up/down, arrow keys), Roll (roll CW/CCW, Z/X)
- Gripper: Open/Close (G/H)
- Gestures: Push/Pull (P/L), Grab (G/H)
Each primitive has a parameter (speed for translation, angular velocity for rotation) and a threshold (e.g., ±0.01 m/s for trucking, ±0.5°/s for panning) that determines when continuous motion discretizes into a discrete action step.

The formal decomposition from Appendix C.2:

$A^{\text{nav}}_i = T_{i \to i+1} = \{\Delta R, \Delta t\} \approx \left\{t_i \cdot v_i, \; t_k \cdot \omega_k \mid i,k \in \{x,y,z\},\; t_i, t_k \in \mathbb{Z}_{\geq 0}\right\}$

where $\Delta R = (\Delta R_x, \Delta R_y, \Delta R_z)$ are the rotation components from Euler decomposition, $\Delta t = (\Delta t_x, \Delta t_y, \Delta t_z)$ are translation components, and $t_i, t_k$ are discrete integer step counts bounded by the video frame rate.

What it computes: Each frame-to-frame camera transformation is decomposed into axis-aligned translation and rotation components, then quantized into integer multiples of fixed step sizes. For example, a forward movement of 0.25 meters over 4 frames becomes "Dolly In" with step count 4. This converts continuous video motion into a sequence of discrete natural language actions.

Why this form: MLLMs output text tokens, not continuous control signals. By discretizing motion into named primitives with integer step counts, the action space becomes expressible in language while remaining executable in metric environments. The naming scheme (Truck, Dolly, Pedestal, Pan, Tilt, Roll) draws from cinematography terminology, making the action space intuitive for language models that have been exposed to film and video production language in their pretraining data.
Human Annotation Pipeline: For egocentric manipulation videos, human annotators create multi-option action sequences formatted as multiple-choice tasks. Each frame provides candidate action options, and the annotator selects the correct next action. For the final frame, annotators provide a completion flag (1 for successful task completion, 0 for incomplete). This produces evaluation data that tests whether a model can select appropriate actions in sequence without requiring it to generate free-form action commands.
Goal-Driven Task Formulation: For navigation, the evaluation presents paired images (current state and goal state) and asks the model to generate the action sequence to move from start to goal. An example action sequence is provided (from an earlier image pair) to demonstrate the format. For manipulation, the model receives start and target state images and must generate a sequence of 7-DoF actions. The prompts include detailed action space descriptions, unit step sizes (0.0626 meters per translation step, 0.0725 radians per rotation step), and structured JSON output format requirements.

Evaluation Metrics: Level-Appropriate Measurement

The benchmark uses four categories of evaluation metrics, distributed as 70.7% multiple-choice, with the remainder split across numeric metrics, LLM-as-a-Judge, and agentic execution scores (Figure 4). Each level of the taxonomy gets metrics appropriate to its cognitive demands.

Multi-Option QAs (L1-L3, primary format). Standard accuracy—does the model select the correct option from a predefined set? The multiple-choice format is used for "low- and mid-level capabilities in the SpatialTree (L1–L3)" because it provides objective, unambiguous scoring for tasks where the correct answer is well-defined. The paper explicitly maps ability categories to question formats: perceptual tasks like distance estimation are tested both as multi-option (depth ordering, relative comparison) and as numeric prediction.

Numeric QAs (L1). For tasks requiring continuous quantity prediction (distances, angles, 3D coordinates), the evaluation metric is relative error:

$\text{Relative Error} = \frac{|\hat{y} - y|}{|y|}$

where $\hat{y}$ is the model's predicted value and $y$ is the ground truth.

What it computes: The absolute difference between prediction and ground truth, normalized by the ground-truth magnitude. This produces a dimensionless fraction where 0 is perfect prediction and values >1 indicate errors exceeding the ground-truth value.

Why relative error: Absolute error would penalize the same physical mistake differently depending on scale—a 0.1-meter error in a 1-meter distance (10% error) is a larger relative mistake than a 0.1-meter error in a 10-meter distance (1% error). Relative error correctly reflects that proportional accuracy is what matters for spatial judgment. For very small ground-truth values, this metric becomes unstable, but the paper's datasets (indoor scenes, object scales) operate in regimes where distances are substantial enough to avoid this issue.

For orientation estimation specifically, the evaluation uses a probabilistic scoring function rather than simple angular error. This is documented in Appendix C.1:

$S(y_{\text{pred}}, y_{\text{gt}}, \sigma_{\text{gt}}) = \exp\left(-\frac{(y_{\text{pred}} - y_{\text{gt}})^2}{2\sigma_{\text{gt}}^2}\right)$

where $y_{\text{pred}}$ is the MLLM's predicted angle (pitch, roll, or vFOV), $y_{\text{gt}}$ is the ground-truth value from GeoCalib, and $\sigma_{\text{gt}}$ is GeoCalib's reported uncertainty (standard deviation) for that estimate.

What it computes: A Gaussian similarity score between 0 and 1, where 1 is perfect agreement and the score decays smoothly as prediction error increases. The decay rate is controlled by the ground-truth uncertainty: when GeoCalib is uncertain (large $\sigma_{\text{gt}}$ ), the scoring is more lenient; when it is confident (small $\sigma_{\text{gt}}$ )`, the scoring is stricter.

Why this form: Simple absolute angular error does not account for annotation uncertainty—two predictions could be equally "correct" if they fall within the measurement noise, but absolute error would score the one closer to the point estimate higher. The Gaussian kernel with uncertainty scaling gives partial credit for predictions within the confidence interval, making the metric fair when ground truth itself is imperfect. The final orientation score averages the Gaussian similarities across pitch, roll, and vFOV.

GPT Judge (L3-L4). For open-ended responses or complex reasoning outputs (trajectory descriptions, action sequence explanations), an LLM-based judge evaluates whether the generated response satisfies task requirements, optionally scoring partial correctness. This format is applied primarily to mid- and high-level capabilities where rigid matching against a single ground-truth answer would fail to capture partially correct reasoning.

Agentic Evaluation (L4). This is the most complex metric suite because agentic tasks require multi-dimensional assessment. For navigation, the evaluation combines relative distance and directional accuracy:

$\text{Relative Distance Score: } s_d = \max\left(0, 1 - \frac{\|\Delta p_{\text{pred}} - \Delta p_{\text{gt}}\|}{\|\Delta p_{\text{gt}}\|}\right)$

where $\Delta p_{\text{pred}}$ is the predicted translation vector and $\Delta p_{\text{gt}}$ is the ground-truth translation vector for a single action step.

$\text{Directional Score: } s_\theta = \frac{\Delta p_{\text{pred}} \cdot \Delta p_{\text{gt}}}{\|\Delta p_{\text{pred}}\| \, \|\Delta p_{\text{gt}}\|}$

What they compute: The relative distance score produces a value in $[0, 1]$ where 1 means exact match in translation magnitude and direction, and the score decays linearly as the vector difference grows relative to the ground-truth magnitude. The directional score is the cosine similarity between predicted and ground-truth movement directions, ranging from -1 (opposite) to 1 (identical). The step-wise accuracy is then:

$s_{\text{step}} = s_d \cdot \max(0, s_\theta)$

Why this form: Multiplying distance accuracy by zero-clipped directional accuracy ensures that moving the right amount in the wrong direction (or the right direction but wrong amount) both get penalized. The zero-clipping on $s_\theta$ means that movements in the opposite direction (negative cosine similarity) are treated as complete failures (score 0) rather than receiving fractional credit, which is appropriate because opposing movement is worse than no movement for navigation. The product form ensures both distance and direction must be approximately correct simultaneously—a model cannot compensate for poor direction with precise magnitude or vice versa.

For manipulation, the same translation and direction metrics apply, plus a rotation score and a gripper score. The rotation score normalizes angular error to $[0, 1]$ :

$s_{\text{rot}} = \max\left(0, 1 - \frac{\theta_{\text{err}}}{\pi}\right)$

where $\theta_{\text{err}} = \arccos\left(\frac{\text{Tr}(R_{\text{err}}) - 1}{2}\right)$ with $R_{\text{err}} = R_{\text{pred}} R_{\text{gt}}^T$ being the error rotation matrix.

What it computes: The geodesic angular distance between predicted and ground-truth orientation, normalized by $\pi$ (180 degrees, the maximum possible angular error). A perfect rotation match scores 1, a 90-degree error scores 0.5, and an 180-degree error scores 0.

Why this form: The arccos of the trace formula computes the minimal rotation angle between two orientations in SO(3), which is the correct distance metric for 3D rotations. Normalizing by $\pi$ rather than $2\pi$ reflects that the maximum geodesic distance on SO(3) is $\pi$ , not $2\pi$ . Linear normalization (as opposed to exponential decay) is appropriate here because there is no uncertainty in the ground-truth rotation—the annotation comes from calibrated motion capture or robot kinematics, so the metric should be equally sensitive at all error scales.

The gripper score $s_{\text{gripper}} \in \{0, 1\}$ is binary accuracy on the predicted open/close state.

Metric Aggregation. The final benchmark score is computed through hierarchical weighted summation (Appendix E, Figure H). Each level (L1-L4) receives equal weight of 0.25. Within L1, sub-abilities are weighted as Geometry 0.5, Motion 0.1, Relation 0.15, Localization 0.2, and Orientation 0.1. Within L2, Understanding 0.7 and Memory 0.3. Within L3, Causal Reasoning 0.65 and Sequential Planning 0.35. Within L4, Goal Execution 0.5 and Open Exploration 0.5. The paper justifies these weights through "a synthesis of theoretical principles and empirical, data-driven insights," specifically citing the Pearson correlation analysis (Figure 5) as informing which abilities are most foundational. For example, L1.Geometry receives the highest weight (0.4 × 0.25 = 0.10 of the total score) because it "exhibits strong, widespread correlations with a multitude of other skills" and is "more fundamental to the overall spatial intelligence network."

Models Evaluated. The benchmark evaluates 16 models across three categories (Table 1): Non-Thinking Models (GPT-4o, Gemini 2.5 Flash Nonthinking, Gemini 2.5 Pro Nonthinking), Thinking Models with explicit reasoning mechanisms (Seed1.5VL, Seed1.8, GLM4.5V, Gemini 2.5 Pro, Gemini 2.5 Flash, Gemini 3 Pro, Gemini 3 Flash), and Open-Source Models spanning 7B to 235B parameters (Qwen2.5-VL at 7B, 32B, and 72B; Qwen3-VL at 30B and 235B; Kimi-VL-A3B).

Supervised Fine-Tuning: Testing Transfer Through Targeted Intervention

The SFT experiments are the primary causal methodology for validating the SpatialTree hierarchy. The logic is: if the taxonomy correctly identifies foundational abilities, then fine-tuning a model on a foundational ability should produce measurable improvement in abilities that depend on it, even without explicit training on those dependent abilities. The experiments systematically test this by measuring performance changes across all 27 sub-abilities after training on specific L1 skills.

General Data Mixture Recipe. The authors follow VST's data mixing approach, combining multimodal datasets from LLaVA-Video, LLaVA-NeXT-Interleave, and LLaVA-OneVision to form a general visual-instruction dataset. This covers single-image, multi-image, video, and 3D tasks to provide broad multimodal grounding. The baseline model (referred to as "Baseline" in Table 2) is fine-tuned only on this general data, ensuring that measured improvements in spatial abilities come from the targeted spatial data rather than from general multimodal training.

Targeted SFT Data Construction. For each selected L1 ability, the authors generate approximately 250K QA samples using the SpatialEngine:

L1.Geometry.Distance (B+Dist.): 250K distance-relevant QAs generated from SUNRGBD, Hypersim, and Matterport3D—three datasets that provide RGB-D data or reconstructed 3D geometry from indoor scenes. The training data is augmented with "visual prompts and multi-scale transformations to enhance distance reasoning." The visual prompts likely refer to drawing depth indicator lines or distance markers on images, while multi-scale transformations (image resizing, cropping) force the model to learn scale-invariant distance estimation rather than memorizing pixel-to-depth mappings.
L1.Relation.Correspondence (B+Corr.): 250K matching examples following VST's methodology, generating correspondence data from video sequences and multi-view image pairs where the same point must be identified across different viewpoints.
L1.Geometry.Size (B+Size): 250K samples from 3D bounding-box annotated datasets (SUNRGBD, Hypersim, ArkitScenes), enabling questions about object dimensions, volumes, and relative size comparisons.

The mixing ratio is 1:3—one part targeted spatial data to three parts general visual data. This ratio is chosen to inject spatial-specific knowledge while maintaining general multimodal capabilities. The baseline and each targeted variant consume the same total token count to ensure fair comparison.

Cross-Ability Measurement Protocol. After fine-tuning each variant, the model is evaluated on the full SpatialTree-Bench. This produces a 27-dimensional performance vector for each model variant. The transfer analysis (Table 2) reports changes relative to baseline: positive numbers indicate improvement, negative numbers indicate regression. The key comparisons are:

Intra-level transfer: Does fine-tuning on one L1 ability improve or degrade other L1 abilities? (Finding: negative transfer dominates—B+Dist. improves Geometry by +3.2 but degrades Motion by -2.0, Relation by -5.8, and Localization by -4.6.)
Cross-level transfer: Does fine-tuning on L1 abilities improve L2, L3, and L4 performance? (Finding: positive transfer—B+Dist. improves L2.Understanding by +2.0 and L4.Goal Exec by +3.4.)
Multi-ability synergy: Does joint training on multiple L1 abilities produce gains exceeding the sum of individual effects? (Finding: yes—B+Dist.+Size+Corr. produces +1.1 overall gain, exceeding any individual variant despite individual variants being neutral or negative.)

The authors specifically select three L1 abilities for the SFT study based on the Pearson correlation analysis (Figure 5): "Geometry Distance (L1-Geo.Dist), Geometry Size (L1-Geo.Size), and Relative Correlation (L1-Relat.Corr)" as they "exhibit the strongest correlations with higher-level performance." This is an important methodological choice: they do not randomly sample abilities but select the ones most likely to show transfer effects, making the experiment a test of the dependency hypothesis rather than an unbiased survey.

Reinforcement Learning: Hierarchy-Aware Reward Design

Building on the SFT findings, the RL experiments test whether reinforcement learning with verifiable rewards can scale spatial abilities, and whether the hierarchical structure necessitates differentiated training signals.

Optimization Algorithm. The paper uses Group Relative Policy Optimization (GRPO), a reinforcement learning algorithm designed for language model alignment. GRPO works by generating multiple candidate outputs for each prompt, scoring them with a reward function, and optimizing the policy to increase the probability of high-reward outputs relative to low-reward ones within each group. This is group-relative rather than absolute: rewards are normalized within each batch of candidates, making the training signal invariant to reward scale.

Initial Naive RL Experiments. The first experiments apply uniform GRPO to individual capabilities from each taxonomy level. The results in Table 3 ("Full RL@think" applied to the baseline Qwen2.5-VL-7B) reveal a fundamental tension: while complex reasoning tasks improve under standard RL (L3.Causal Reasoning +5.2, L4.Open Exploration +9.0), perceptual tasks degrade (L2.Understanding -4.1, L3.Sequential Planning -13.0). The paper attributes this to models "overfitting to the specific reward signal" when optimizing for single abilities, producing "siloed improvements that fail to generalize."

Hierarchy-Aware Reward Mechanism (Auto-Think). The central RL innovation is a level-specific reward shaping strategy:

For Intuitive Perception (primarily L1): The reward function explicitly removes credit for "thinking processes"—the model does not receive reward for generating intermediate reasoning tokens. Additionally, a length penalty is applied, "implicitly discouraging the model from over-reasoning on direct visual signals, forcing it to rely on direct visual-text alignment." The motivation is that low-level perception should function as a "fast system" that produces immediate judgments without deliberation.
For Complex Reasoning (L3-L4): The reward function retains and amplifies rewards for explicit reasoning steps, "encouraging the model to utilize more tokens for intermediate computation." This aligns with the chain-of-thought paradigm where additional test-time computation improves reasoning quality.

The auto-think strategy is not a binary switch but a gradient: the reward function is parameterized differently per question, with the taxonomy level of the question determining which reward components are active. Questions tagged as L1 perceptual tasks get the no-thinking reward; questions tagged as L3-L4 reasoning tasks get the thinking-amplified reward. The implementation details (exact reward scaling factors, length penalty coefficients, transition handling for mixed-level batches) are not specified in the main text but would be critical for reproduction.

Experimental Controls for RL Validity. The paper emphasizes two control mechanisms that ensure measured RL improvements reflect genuine capability gains:

Data Decontamination: "The robotic arm data samples used for GRPO training are strictly separated from the SpatialTree-Bench testing data. There is no overlap in specific scenes or object configurations between the training and evaluation sets." This addresses the common concern that RL on benchmark-related data might teach the model to recognize specific scenes rather than general manipulation skills.
Task and Metric Discrepancy: "The training objective is purely maximizing the reward on discrete MCQ selection. In contrast, the SpatialTree-Bench evaluation employs a diverse set of continuous and semantic metrics (e.g., Mean Squared Error for distance, angular error for orientation, and execution success rates for agentic tasks)." This means the model is optimized for multiple-choice accuracy during RL but evaluated on fundamentally different metrics at test time, making simple reward hacking or metric exploitation unlikely.

RL Results Interpretation. The key comparison in Table 3 is between "Full RL@think" (uniform reasoning reward) and "Full RL@auto-think" (hierarchy-aware reward). The auto-think variant shows:

L1 improvements across the board (+3.3 Geometry, +4.0 Motion, +1.3 Relation, +0.8 Orientation) where the think variant showed mixed results (+1.1, +0.1, +6.5, -1.2 respectively)
L2 improvements (+5.8 Understanding vs. +5.2 for think; -0.1 Memory vs. -5.9 for think)
Comparable L3-L4 improvements
Overall average improvement of +3.6 vs. +2.9 for the think variant

The most dramatic reversal is L2.Memory: the think variant degrades it by -5.9, while the auto-think variant is essentially neutral (-0.1). This supports the paper's claim that over-thinking damages tasks requiring direct perceptual memory, and that suppressing unnecessary reasoning during training protects these abilities.

Training Data for RL. The RL experiments use the SFT baseline (referred to as "After SFT" in Table 3) as the starting point, specifically the model described in the SFT section as "B+Dist.+Size+Corr.+Mot." with overall score 27.3. Additional RL experiments apply GRPO to individual taxonomy levels (L1 RL@think, L2 RL@think, L3 RL@think, L4 RL@think) to isolate level-specific effects, with each using only data from that level for reward computation.

Design Choices and Their Justifications

Cognitive science grounding over purely empirical clustering. The taxonomy is derived from Piaget, Tolman, and Kuipers rather than from unsupervised clustering of benchmark results. The justification is that cognitive science provides "developmental progression" logic—abilities that emerge earlier in human development are more foundational—which would not necessarily emerge from correlation analysis alone. However, the paper validates the taxonomy empirically through the Pearson correlation analysis (Figure 5) and the SFT transfer experiments, creating a synthesis of theoretical derivation and empirical validation.

Capability-centric over task-centric organization. The paper argues that by organizing around cognitive functions rather than task formats, the framework enables systematic study of dependencies that task-centric benchmarks obscure. A practical consequence: the same underlying ability (distance perception) can be tested across multiple task formats (multiple-choice, numeric, agentic execution), revealing format-invariant capability versus format-specific learned behaviors. The SFT experiments validate this: training on one distance estimation format transfers to others, indicating the model learns distance awareness rather than task-specific heuristics.

Expert model-based annotation over human annotation for low-level perception. For L1 data generation, the paper uses automated expert models (DepthAnything, SpatialTracker, GeoCalib, OrientAnything) rather than human annotators. This is justified by scale: generating 250K distance QAs with human annotations would be prohibitively expensive. More importantly, expert models provide continuous, metric annotations (exact depth in millimeters, precise orientation angles) that human annotators cannot provide—humans can tell you "object A is closer than object B" but cannot output "object A is 1.87 meters away." This metric precision is essential for the numeric evaluation metrics.

Discrete action primitives over continuous control for L4. The action space uses named primitives with integer step counts rather than raw joint angles or end-effector velocities. This is necessary because MLLMs output language tokens, not floating-point vectors. The cinematography-inspired naming scheme (Truck, Dolly, Pedestal) is a clever design choice that leverages the model's pretraining exposure to film production terminology, potentially providing useful inductive bias for spatial motion concepts.

Unified per-step metrics for agentic evaluation. The navigation and manipulation metrics decompose each action sequence into individual steps, compute per-step scores, then aggregate. This enables fine-grained diagnosis: a model might plan the right direction (high $s_\theta$ ) but wrong magnitude (low $s_d$ ), indicating a specific weakness in metric estimation rather than directional reasoning. A single end-to-end success rate would lose this diagnostic information.

Uncertainty-aware scoring for orientation. The Gaussian kernel metric for orientation estimation (Appendix C.1) is unusual in benchmark design. Most benchmarks use deterministic ground truth and score predictions against it. The paper's approach acknowledges that ground-truth orientation annotations from GeoCalib have heterogeneous uncertainty—some images are intrinsically harder to calibrate than others—and the metric should reflect this. This is a more principled evaluation than treating all predictions equally regardless of annotation quality.

The auto-think reward design as a training-time intervention, not an inference-time strategy. It is important to note that auto-think operates during RL training, not evaluation. The model learns to suppress unnecessary reasoning during training through reward shaping, and this becomes an internalized behavior that manifests at inference without requiring explicit "think/don't think" prompts. This is different from prompting strategies that tell the model to reason or not reason at test time—theauto-think approach modifies the model's learned policy, not just its test-time behavior. The paper does not explicitly discuss this training-vs-inference distinction, but it is implicit in the RL methodology.

4. Key Insights and Innovations

Innovation 1: Capability-Centric Taxonomy as a Diagnostic Tool, Not Just a Classification Scheme

The fundamental intellectual move of this paper is not that spatial abilities can be categorized—cognitive science has done that for decades—but that a capability-centric taxonomy can function as a causal diagnostic instrument for understanding how abilities relate within trained models. This is a qualitatively different use of taxonomy than what appears in prior benchmarks.

In task-centric benchmarks (BLINK, SpatialEval, VSI-Bench, MMSI-Bench, Omnispatial), categorization serves an organizational purpose: group similar tasks together so results are readable. The taxonomy is descriptive—it tells you what was tested, not why performance patterns emerge. A model scoring 40% on "spatial reasoning" and 60% on "spatial understanding" leaves you with no framework for determining whether the gap reflects genuine capability differences, task difficulty confounding, or measurement noise.

SpatialTree repurposes taxonomy as a hypothesis-generating instrument. By organizing abilities into a dependency hierarchy (L1 → L2 → L3 → L4), the framework makes specific, falsifiable predictions: training on L1 abilities should transfer to L2-L4 but not vice versa; abilities at the same level may interfere with each other if they compete for shared representational capacity; higher-level abilities should show stronger inter-correlation because they share foundational prerequisites. These are not organizational claims—they are causal claims about model internals.

What makes this genuinely novel is that the paper tests these predictions through targeted training interventions (Section 6.1, Table 2), treating the taxonomy as a scientific model rather than a filing system. The finding that individual L1 SFT produces negative intra-level transfer but positive cross-level transfer (+2.0 on L2.Understanding, +3.4 on L4.Goal Exec from distance training) is not just an empirical result—it validates the taxonomy's structural claim that L1 abilities are prerequisites for higher levels while being mutually interfering at the same level. A purely descriptive taxonomy could never produce this insight because it wouldn't specify which relationships to test.

This reframes what benchmarks are for. Rather than asking "which model is best at spatial reasoning?" (the task-centric question), the capability-centric question becomes "what is the dependency structure of this model's spatial abilities, and where are the bottlenecks?" The distinction matters practically: if a model fails at L3 causal reasoning, the taxonomy tells you to check whether the failure originates in L1 distance perception (a fixable training gap) or in genuine reasoning deficits (a harder architectural limitation). Prior benchmarks could tell you the model failed; SpatialTree tells you where in the cognitive stack to look for the cause.

This is a fundamental reframing, not an incremental improvement. It changes benchmarks from measurement instruments into diagnostic instruments. The field has seen analogous shifts in other domains—from task-specific NLP benchmarks to capability probing suites, from monolithic accuracy metrics to fine-grained error analysis—but spatial intelligence in MLLMs had not undergone this transition before SpatialTree.

Innovation 2: Negative Intra-Level Transfer with Positive Cross-Level Transfer as a Structural Property

The SFT transfer experiments (Table 2) reveal a pattern that is surprising under standard assumptions about neural network training and has significant implications for how spatial abilities should be trained. The pattern: individual L1 ability fine-tuning harms other L1 abilities while improving higher-level abilities, and joint L1 training produces synergistic gains exceeding the sum of individual effects.

Why this is surprising. The default assumption in multi-task learning is that training on related tasks produces positive transfer—shared representations benefit all tasks. Under this assumption, fine-tuning on L1 distance estimation should either improve or leave unchanged other L1 abilities like motion perception or size estimation, since they all involve visual-spatial processing from the same input modality. The data contradict this: B+Dist. improves Geometry by +3.2 but degrades Motion by -2.0, Relation by -5.8, and Localization by -4.6. The model is not just failing to transfer—it is actively losing capability in untrained L1 skills.

The paper's interpretation, though not fully mechanistically explained, points toward representational competition: L1 abilities may rely on partially overlapping early visual processing pathways, and optimizing for one ability's output format (e.g., distance regression) shifts those shared representations in ways that are maladaptive for other abilities' output formats (e.g., correspondence matching). This is a form of negative transfer that is well-documented in continual learning but rarely characterized at the level of cognitive abilities within a single model.

Why cross-level transfer works despite intra-level interference. The same distance training that degrades other L1 skills improves L2.Understanding (+2.0) and L4.Goal Exec (+3.4). Figure 6 provides qualitative evidence for the mechanism: the model trained on simple distance QAs (object depth sorting, depth comparison in synthetic and indoor scenes) generalizes to complex in-the-wild distance reasoning (+36.0%) and even robotic arm manipulation (+27.1%). This suggests that L1 training teaches a capability primitive—distance awareness—that is format-agnostic enough to be recombined with other primitives at higher levels. Higher-level tasks may use distance as one input among many, so improving that input improves the composite even if other low-level primitives have degraded.

Multi-ability synergy as evidence for compositional structure. The most striking result in Table 2 is that B+Dist.+Size+Corr. (+1.1 overall) outperforms any individual variant (B+Dist. -0.5, B+Corr. +0.2, B+Size -1.5) and even reverses negative intra-level effects: L1.Motion, which suffered under individual training (best individual change -2.0), shows +0.7 under joint training. This is not additive—it is synergistic. The paper's interpretation is that joint training prevents representational collapse toward any single L1 output format, instead forcing the model to maintain flexible spatial representations that serve multiple perceptual judgments simultaneously.

This finding has direct practical implications that challenge current training paradigms. The common practice of curating broad, mixed datasets for SFT (throw everything at the model) is partially vindicated by the synergy result—but the negative intra-level transfer from single-ability training suggests that targeted fine-tuning on narrow spatial skills is dangerous if done in isolation. You cannot simply improve a model's distance estimation by fine-tuning on distance data and expect other spatial skills to be unaffected; you must either train holistically or accept collateral damage.

This is a conceptual advance with immediate methodological consequences, grounded in the specific transfer patterns of Table 2 and the qualitative evidence of Figure 6. It is not merely an empirical observation but a structural claim about how spatial abilities are organized in MLLM representations—as partially competing at the perceptual level but composable at higher cognitive levels.

Innovation 3: The Reasoning-Perception Trade-Off as a Training Principle (Auto-Think)

The RL experiments (Section 6.2, Table 3) uncover a phenomenon that has implications beyond spatial intelligence: the optimization pressure toward explicit reasoning that benefits complex tasks can actively damage intuitive perceptual abilities, and this trade-off can be managed through level-specific reward design.

What prior work assumed. The dominant paradigm in reasoning-augmented LLMs—from chain-of-thought prompting to DeepSeek-R1 and OpenAI O1—treats explicit step-by-step reasoning as uniformly beneficial. More thinking tokens → better answers. This assumption has driven architectural decisions (reasoning budgets, test-time compute scaling) and training strategies (RL with reasoning rewards). The possibility that "thinking" could hurt performance on certain task types was not seriously entertained, because the tasks where reasoning helps (math, logic, planning) were the focus of evaluation.

What the RL experiments reveal. The "Full RL@think" variant in Table 3, which applies uniform reasoning rewards across all spatial tasks, produces a stark divergence: complex reasoning improves (L3.Causal Reasoning +5.2, L4.Open Exploration +9.0) while perceptual and memory tasks degrade (L2.Understanding -4.1, L2.Memory -2.1, L3.Sequential Planning -13.0). The degradation of Sequential Planning is particularly notable—a -13.0 drop is catastrophic—and suggests that over-thinking during RL training teaches the model to approach plan generation with verbose deliberation that backfires for tasks requiring efficient, direct action sequence generation.

The auto-think strategy (Full RL@auto-think) resolves this divergence by applying differentiated rewards: suppressing thinking rewards and adding length penalties for L1 perceptual tasks, while amplifying reasoning rewards for L3-L4 tasks. The result is uniform improvement across levels (+3.6 overall vs. +2.9 for Full RL@think) with the most dramatic reversals in the tasks that naive RL damaged: L2.Memory goes from -5.9 (think) to -0.1 (auto-think), L1.Geometry from +1.1 to +3.3, L1.Motion from +0.1 to +4.0.

Why this is conceptually significant. The auto-think result challenges the universality of the "reasoning is good" assumption by demonstrating that perceptual tasks benefit from a different optimization objective than reasoning tasks. This maps onto the dual-process theory from cognitive psychology (System 1: fast, intuitive; System 2: slow, deliberative), but with a crucial distinction: the paper shows this is not just a descriptive framework but an actionable training principle. The same model can develop both fast and slow processing modes if reward signals are structured appropriately during RL.

This finding has implications beyond spatial intelligence. Any domain where some tasks require intuitive judgments (perception, fluency, aesthetic assessment) and others require deliberative reasoning (planning, proof, multi-step inference) may exhibit the same trade-off under uniform RL. The auto-think strategy provides a template: identify which tasks in your domain are perceptual vs. reasoning-heavy, and shape rewards accordingly.

The paper does not claim auto-think is a fundamental algorithmic contribution—GRPO is standard, and level-specific reward shaping is a straightforward extension. The innovation is diagnostic: identifying that the reasoning-perception trade-off exists in spatial ability training, and demonstrating that a simple differentiated strategy can resolve it. This is a conceptual insight that changes how researchers should think about training spatial (and potentially other) abilities in MLLMs, supported by the before/after comparison in Table 3.

Innovation 4: Integrating Agentic Competence into a Spatial Intelligence Hierarchy

The inclusion of L4 Agentic Competence as the top level of SpatialTree is a conceptual contribution that reframes the relationship between spatial reasoning and embodied action. Prior work treated these as separate research threads: spatial reasoning benchmarks (VSI-Bench, MMSI-Bench, Omnispatial) evaluated static understanding of space, while embodied benchmarks (EmbodiedBench) evaluated interactive task completion. The two communities largely did not talk to each other.

What SpatialTree does differently. By positioning agentic competence as the culmination of perception (L1), mapping (L2), and simulation (L3), the taxonomy makes a specific theoretical claim: embodied action is not a separate capability but the integration of lower-level spatial abilities in an interactive loop. The formal model in Section 3.4 makes this explicit:

$(S_t, A_t, M_t) \sim P_\theta(\cdot \mid O_t, H_{t-1})$

This formulation embeds perception (processing $O_t$ ), memory (updating $M_t$ from history $H_{t-1}$ ), and planning (selecting $A_t$ based on latent state $S_t$ ) into a unified decision loop. An agent's ability to navigate or manipulate is not a single monolithic skill but the dynamic composition of all lower-level capabilities under closed-loop control.

Evidence for the integration claim. The SFT transfer experiments provide causal evidence: training on L1 distance estimation improves L4 goal execution (+3.4 for B+Dist., +3.9 for the joint training variant in Table 2). This is not an obvious result—one might expect that low-level perceptual training would have no bearing on complex action generation. The fact that it does transfer supports the hierarchy's claim that agentic competence depends on foundational perception. Figure 6 visualizes this transfer concretely: a model trained on simple depth comparison QAs produces more reasonable robotic arm control sequences, suggesting that better metric spatial awareness directly improves action selection in 3D space.

What this enables. The integration creates a unified evaluation framework where the same model can be diagnosed from perception through action. A model that fails at L4 navigation can be traced backward: is the failure in action selection (L4-specific), in planning (L3), in spatial memory (L2), or in basic depth perception (L1)? The correlated improvements across levels under SFT and RL suggest that interventions targeting lower levels can cascade upward, making the hierarchy a roadmap for efficient capability improvement.

This is an architectural reframing, not an incremental benchmark extension. It changes the question from "how good is this model at spatial reasoning?" and "how good is this model at embodied tasks?" (two separate questions) to "how does this model's spatial intelligence manifest across the full stack from perception to action?" (one integrated question). The significance is both diagnostic (understanding failure modes) and strategic (identifying leverage points for improvement).

The limitation, which the paper does not fully resolve, is that L4 evaluation remains the least developed part of the benchmark. The goal-driven navigation and manipulation tasks (Appendix C.2) use simplified action spaces (discrete primitives, paired-image goals) that abstract away many challenges of real embodied interaction (continuous control, partial observability, physical dynamics). The integration is conceptually powerful but practically constrained by the difficulty of evaluating open-ended agentic behavior at scale. This is not a weakness of the paper's contribution so much as a frontier it opens for future work.

Innovation 5: The Demonstration That Spatial Abilities Are Not Monolithic—And That This Matters for Training

A recurring theme across the paper's experiments is that spatial abilities do not scale uniformly, and that treating them as a monolithic construct leads to suboptimal outcomes. This finding is deceptively simple but has deep implications.

Prior implicit assumption. The standard approach to improving spatial intelligence in MLLMs—exemplified by VST (Visual Spatial Tuning) and general multimodal SFT recipes—is to curate diverse spatial data and train on all of it together. The implicit assumption is that spatial ability is a general competency that improves with more spatial data, analogous to how language ability improves with more text. Under this assumption, data diversity matters primarily for coverage, not because different abilities require different training treatments.

What the experiments show instead. Multiple lines of evidence converge on the non-monolithic nature of spatial abilities:

The Pearson correlation matrix (Figure 5): L1 abilities show weak inter-correlation (region B), indicating they are largely independent perceptual modules rather than expressions of a single underlying "spatial perception" factor. In contrast, L3-L4 abilities show strong correlations (region A), suggesting they share common cognitive infrastructure despite being different tasks.
Negative intra-level transfer under SFT (Table 2): The fact that training on distance degrades motion, relation, and localization demonstrates that L1 abilities are not just independent but can be antagonistic—optimizing for one can suppress others. This would not happen if spatial perception were a unitary construct.
Differential RL effects (Table 3): The same RL optimization that improves causal reasoning (+5.2) degrades sequential planning (-13.0) in the naive RL condition. These are both L3 abilities, yet they respond oppositely to uniform training pressure.
The auto-think necessity: The fact that a level-specific reward strategy is required to achieve uniform improvement across all abilities demonstrates that different types of spatial cognition require different optimization signals.

Why this matters beyond this paper. The non-monolithic finding challenges a broader assumption in MLLM development: that capabilities can be improved by adding more data from the target domain without careful attention to the structure of abilities within that domain. If spatial abilities are modular and partially competing rather than unitary and additive, then data curation and training strategy must be informed by an understanding of which abilities support versus interfere with each other. The paper provides the diagnostic framework (SpatialTree) and the causal methodology (targeted SFT + cross-ability evaluation) for building this understanding.

This is a conceptual correction to a widespread implicit assumption, supported by converging evidence across static evaluation (Figure 5), SFT interventions (Table 2), and RL experiments (Table 3). It is not a positive result—it is a cautionary finding that says "your uniform training strategy is leaving performance on the table and may be actively damaging some abilities." The paper's positive contribution is providing the toolkit to do better, but the diagnostic finding itself is the innovation.

5. Experimental Analysis

Evaluation Methodology

Dataset. The paper uses the SpatialTree-Bench, a newly constructed dataset built by reorganizing questions from prior spatial benchmarks (Omnispatial, MMSI-Bench, CameraBench, SpatialEval, 3DSR-Bench, VSI-Bench, SpatialViz-Bench, IR3D-Bench, EmbodiedBench, LLaVA-3D, Multi-SpatialMLLM) and augmenting them with SpatialPlus, a complementary dataset targeting missing capabilities (L1 Orientation, L1 Shape, L2 Spatial Caption, L4 Agentic Competence). The resulting benchmark evaluates 27 sub-abilities organized into the four-level hierarchy. The SFT transfer experiments use targeted training data generated from SUNRGBD, Hypersim, Matterport3D, Co3dv2, ArkitScenes, and TartanAir, with approximately 250K QA samples per ability. For L4, agentic data is drawn from Miradata (game footage), EgoDex (egocentric manipulation), and Droid (robotic manipulation). The paper does not report a single total benchmark size, but the distribution across 41 tasks with 70.7% multiple-choice questions (Figure 4) suggests a substantial evaluation set.
Base model(s). The primary evaluation in Table 1 covers 16 models spanning three categories: Non-Thinking Models (GPT-4o, Gemini 2.5 Flash NT, Gemini 2.5 Pro NT), Thinking Models with explicit reasoning mechanisms (Seed1.5VL, Seed1.8, GLM4.5V, Gemini 2.5-Pro, Gemini 2.5-Flash, Gemini 3-Pro, Gemini 3-Flash), and Open-Source Models (Qwen2.5-VL at 7B, 32B, and 72B; Qwen3-VL at 30B and 235B; Kimi-VL-A3B). For the SFT transfer experiments (Section 6.1, Table 2), the base model is not explicitly named but is described as following the VST data mixing recipe and is likely an unspecified baseline fine-tuned only on general visual-instruction data. The RL experiments (Section 6.2, Table 3) use Qwen2.5-VL-7B as the starting point, with the SFT baseline (score 27.3) as the intermediate checkpoint from which additional RL is applied. The choice of Qwen2.5-VL-7B for RL experiments is pragmatic: it is the smallest open-source model evaluated, making RL training computationally tractable while providing a meaningful baseline to measure improvement against.
Metrics. The benchmark uses four metric categories distributed as shown in Figure 4. Multi-Option QAs (70.7%): standard accuracy on selecting the correct option from a predefined set, applied to L1-L3 capabilities. Numeric QAs: relative error defined as |\hat{y} - y| / |y| for distance, angle, and 3D coordinate predictions. For orientation estimation specifically, a Gaussian similarity score S(y_pred, y_gt, σ_gt) = exp(-(y_pred - y_gt)² / (2σ_gt²)) is used, where σ_gt is GeoCalib's reported uncertainty, enabling uncertainty-aware scoring (Appendix C.1). GPT Judge: LLM-based evaluation for open-ended reasoning tasks (L3-L4), assessing whether generated responses satisfy task requirements with optional partial credit. Agentic Evaluation (L4): for navigation, per-step accuracy combines relative distance score s_d = max(0, 1 - ||Δp_pred - Δp_gt|| / ||Δp_gt||) and directional score s_θ = (Δp_pred · Δp_gt) / (||Δp_pred|| ||Δp_gt||) into a combined metric s_step = s_d · max(0, s_θ) that requires both translation magnitude and direction to be approximately correct simultaneously. For manipulation, this is extended with a rotation score s_rot = max(0, 1 - θ_err / π) where θ_err is the geodesic angular distance, and a binary gripper score s_gripper ∈ {0, 1}. Scores are aggregated hierarchically using the weighting scheme in Appendix E, Figure H.
Baselines. The primary evaluation in Table 1 compares all models against each other without a single designated baseline—the table itself serves as the comprehensive comparison, with dark gray highlighting the overall best result and light gray indicating the best open-source result. For the SFT experiments (Table 2), the Baseline is a model fine-tuned only on general visual-instruction data (from LLaVA-Video, LLaVA-NeXT-Interleave, LLaVA-OneVision) with the same token consumption as the targeted variants, isolating the effect of the spatial data from general multimodal training improvements. Each targeted variant (B+Dist., B+Corr., B+Size) adds ability-specific data at a 1:3 ratio with general data. For RL experiments (Table 3), the baseline is the untuned Qwen2.5-VL-7B (score 27.5), and the starting point for RL is the SFT model (score 27.3, the "After SFT" baseline from the compound training variant B+Dist.+Size+Corr.+Mot.). The RL comparisons include level-specific variants (L1 RL@think, L2 RL@think, etc.) and the two full variants (Full RL@think, Full RL@auto-think).
Generation budget / compute accounting. For the SFT experiments, all variants consume the same total token count to ensure fair comparison, though the exact token count is not specified. The RL experiments use GRPO without specifying generation budgets per training step. In evaluation, there is no explicit compute budget constraint—models are evaluated on benchmark accuracy without controlling for inference-time computation. This means the benchmark measures capability, not efficiency, and does not account for potential differences in test-time compute usage between thinking and non-thinking models. The paper does not discuss FLOPs or inference cost equivalence between models of different scales or between reasoning-augmented and standard models, which could confound comparisons—a thinking model that uses more tokens per answer might achieve higher accuracy through additional computation rather than superior spatial ability per se.
Cross-validation / statistical protocol. The SFT experiments use a straightforward pre-post design: train each variant on its targeted data, then evaluate on the full SpatialTree-Bench. There is no mention of cross-validation, multiple training runs, or confidence intervals for the transfer measurements in Table 2. The RL experiments enforce two control mechanisms: (1) data decontamination—robotic arm training data is "strictly separated from the SpatialTree-Bench testing data" with "no overlap in specific scenes or object configurations," and (2) task and metric discrepancy—the training objective maximizes MCQ selection reward while evaluation uses continuous metrics (MSE for distance, angular error for orientation, execution success rates for agentic tasks), making simple reward hacking unlikely. However, the paper does not report statistical significance tests, standard deviations across runs, or effect size confidence intervals for any of the transfer results. The Pearson correlation analysis (Figure 5) is computed across the 16 evaluated models—a sample of 16 data points per ability pair—which provides limited statistical power for identifying fine-grained dependency structures. The two-fold cross-validation protocol described in the reference paper for compute-optimal strategy selection is not used here; the transfer experiments are single-run measurements.

Main Quantitative Results

Overall Benchmark Performance

Table 1 presents the comprehensive evaluation of 16 models across the SpatialTree-Bench. The top-performing model is Gemini 3 Flash with an overall score of 57.8, followed closely by Gemini 3 Pro at 56.5. Among open-source models, Qwen3-VL-235B leads at 40.0, with Qwen3-VL-30B at 35.3 and Qwen2.5-VL-72B at 33.0. The worst-performing model is Kimi-VL-A3B at 24.4.

Several structural patterns emerge from the per-ability breakdown in Table 1:

L1 abilities show high variance across models. On Geometry, Gemini 3 Pro achieves 54.5 while Qwen2.5-VL-7B scores only 17.8—a 3× gap. On Orientation, the spread is even wider: Gemini 3 Pro achieves 74.0 (the highest single-ability score in the entire table) while Kimi-VL-A3B scores 21.4. This suggests that basic spatial perception, despite being "low-level," is far from solved and varies dramatically with model scale and architecture.
L2 Memory shows the widest gap between thinking and non-thinking models. Gemini 3 Flash achieves 66.8 on L2.Memory while GPT-4o scores 43.6, and Qwen2.5-VL-7B scores only 15.2—the lowest score for any model on any ability. This is consistent with the hypothesis that memory tasks benefit from explicit reasoning about spatial relationships across frames.
L4 Agentic Competence remains low across all models. Goal Execution scores range from 14.1 (Qwen2.5-VL-32B) to 31.6 (Gemini 3 Flash), with most models clustering between 24-30. Open Exploration scores are higher (25.9 to 70.8) but also show no model achieving dominance. This confirms that agentic spatial tasks remain challenging even for state-of-the-art MLLMs, with the best model achieving only 31.6% on goal-driven execution tasks.
Non-thinking models are competitive on L1 but fall behind on L3-L4. GPT-4o achieves 38.6 on L1.Motion (vs. 40.7 for Gemini 3 Flash) and 36.2 on L1.Orientation (vs. 54.6), but trails significantly on L3.Causal Reasoning (29.3 vs. 58.4) and L4.Open Exploration (39.2 vs. 70.8). This validates the SpatialTree hierarchy: reasoning augmentation primarily benefits the top of the tree, not the perceptual foundation.

A notable anomaly: Seed1.8 achieves 70.6 on L4.Open Exploration while scoring only 26.0 on L4.Goal Execution—a 44.6-point gap within the same level. This suggests that open-ended exploration and goal-driven execution, despite being grouped under L4, may require substantially different capabilities, or that the evaluation formats (free-form vs. structured action generation) advantage different model architectures.

SFT Transfer Experiments: Intra-Level Interference and Cross-Level Transfer

Table 2 reports the core transfer results, with all changes measured relative to the Baseline (overall score 25.0).

Finding 1: Negative intra-level transfer from single-ability L1 training. Individual L1 SFT produces consistent degradation in untrained L1 abilities:

B+Dist. (distance training): Improves Geometry by +3.2 but degrades Motion by -2.0, Relation by -5.8, and Localization by -4.6. Net overall change: -0.5.
B+Corr. (correspondence training): Degrades Geometry by -3.2, Motion by -4.7, and Localization by -5.3, while improving Relation by +1.3 (since correspondence is a sub-component of Relation). Net overall: +0.2.
B+Size (size training): Improves Geometry by +3.4 but degrades Motion by -6.0, Relation by -7.5, and Localization by -2.5. Net overall: -1.5.

The pattern is consistent: any single-ability L1 training degrades at least two other L1 abilities, with degradation magnitudes (typically -2 to -7.5) often exceeding the gains in the trained ability (+3.2 to +3.4). This is strong evidence that L1 abilities compete for shared representational capacity.

Finding 2: Positive cross-level transfer despite intra-level interference. The same training that harms other L1 skills improves higher-level abilities:

B+Dist. improves L2.Understanding by +2.0 and L4.Goal Exec by +3.4, while leaving L2.Memory and most L3 abilities approximately neutral.
B+Corr. improves L2.Memory by +2.9, L3.Sequential Planning by +2.2, L4.Goal Exec by +2.6, and L4.Open Exploration by +9.4—the largest single cross-level gain observed.
B+Size shows minimal cross-level transfer (most L2-L4 changes are negative or neutral), suggesting that size estimation alone is less useful for higher-level tasks than distance or correspondence.

Figure 6 provides qualitative evidence for the mechanism: a model trained on simple distance QAs (object depth sorting, depth comparison in synthetic/indoor scenes) generalizes to complex in-the-wild distance reasoning with a 36.0% gain and to robotic arm manipulation with a 27.1% gain. The figure shows the model successfully applying distance awareness to tasks with novel coordinate prompts and multiple queried points, and producing more reasonable gripper control sequences, without having seen these specific task formats during training.

Finding 3: Multi-ability synergy from joint L1 training. The compound training variant B+Dist.+Size+Corr. achieves an overall gain of +1.1, exceeding all individual variants (best individual: B+Corr. at +0.2). More importantly, it reverses negative intra-level effects: L1.Motion, which degraded by -2.0 to -6.0 under individual training, shows +0.7 under joint training. Similarly, L1.Relation goes from individual changes of -5.8 to +1.3 to +0.5 under joint training. The synergy is not merely additive—the sum of individual effects on L1.Motion would be negative (roughly -2.0 + -4.7 + -6.0 = -12.7), yet joint training produces +0.7. The paper attributes this to joint training preventing "representational collapse toward any single L1 output format, instead forcing the model to maintain flexible spatial representations that serve multiple perceptual judgments simultaneously."

Adding Motion data (B+Dist.+Size+Corr.+Mot.) further increases overall gain to +2.3, with L1.Geometry reaching +7.7 and L4.Open Exploration reaching +9.4. However, some L1 abilities still degrade (Motion -4.0, Relation -8.3), suggesting that even joint training cannot fully eliminate intra-level competition.

A control experiment ("Baseline+75@(all spat.)" in Table 2) trains on all spatial data at 75% of the sequencing length, consuming the same tokens. This variant degrades to 23.6 (-1.4 relative to baseline), with negative changes across most abilities (L1.Motion -6.0, L1.Relation -3.0, L1.Localization -6.8, L1.Orientation -3.0, L3.Causal Reasoning -1.5, L3.Sequential Planning -1.5, L4.Goal Exec -2.4, L4.Open Exploration -3.7). The paper does not elaborate on this result, but it suggests that simply mixing all spatial data without the careful ability-by-ability training protocol used in the targeted SFT experiments is counterproductive—possibly because the model cannot effectively learn from such diverse spatial signals simultaneously at limited token budgets.

RL Experiments: The Reasoning-Perception Trade-Off

Table 3 reports RL results, with Qwen2.5-VL-7B (score 27.5) as the base and the SFT model (score 27.3) as the starting point for RL.

Finding 4: Level-specific RL produces different effects at different levels. When GRPO is applied to individual taxonomy levels (starting from the SFT baseline of 27.3):

L1 RL@think: Overall score drops to 26.6 (-0.7). L1.Motion improves (+5.4), L1.Relation improves dramatically (+9.9), but L1.Localization degrades severely (-6.8) and L2.Memory degrades (-4.1). The net effect is negative, showing that optimizing for L1 tasks in isolation produces the same intra-level interference pattern observed in SFT, compounded by cross-level degradation.
L2 RL@think: Overall 26.7 (-0.5). L2.Understanding improves (+4.5), but L1.Geometry degrades (-4.1) and L2.Memory degrades (-6.5). Optimizing mapping abilities damages perceptual foundations.
L3 RL@think: Overall 27.7 (+0.4). L3.Causal Reasoning improves (+3.1), L2.Understanding improves (+3.9), L4.Goal Exec improves (+3.2), but L1.Geometry degrades dramatically (-12.3)—the largest single-ability drop in any experiment. This is the clearest evidence that reasoning-heavy optimization can severely damage perceptual abilities.
L4 RL@think: Overall 28.5 (+1.2). L4.Goal Exec improves (+3.9), L3.Causal Reasoning improves (+3.8), but L1.Geometry degrades (-4.8) and L1.Orientation degrades (-2.1). Even optimizing for the highest level of the hierarchy damages the perceptual foundation.

The consistent pattern across all level-specific RL experiments is that gains in the target level come at the cost of L1 perceptual degradation, with L1.Geometry suffering in every single variant (ranging from -4.1 to -12.3).

Finding 5: Uniform "thinking" RL produces gains in reasoning but losses in perception. The Full RL@think variant (applying uniform reasoning rewards across all levels, starting from the SFT baseline) achieves an overall improvement of +2.9 (from 27.3 to 30.1). However, this masks a sharp divergence:

Gains: L1.Relation +6.5, L2.Understanding +5.2, L3.Causal Reasoning +5.5, L3.Sequential Planning +4.8, L4.Open Exploration +5.8
Losses: L2.Memory -5.9, L1.Localization -5.3, L2.Memory (and possibly others)

The pattern mirrors the level-specific results: reasoning-heavy abilities improve while memory and localization degrade. The paper's interpretation is that encouraging extensive "thinking" tokens during RL teaches the model to deliberate, which helps for complex reasoning but interferes with tasks requiring direct, intuitive judgments.

Finding 6: Auto-think resolves the trade-off. The Full RL@auto-think variant (hierarchy-aware reward: suppress thinking for L1, amplify for L3-L4) achieves an overall improvement of +3.6 (from 27.3 to 30.8), outperforming Full RL@think (+2.9). The key improvements over the think variant:

L1: Geometry +3.3 vs. +1.1, Motion +4.0 vs. +0.1, Orientation +0.8 vs. -1.2
L2: Memory -0.1 vs. -5.9 (essentially neutral vs. severe degradation)
L3-L4: performance is comparable or slightly worse (L3.Sequential Planning +2.8 vs. +4.8, L4.Goal Exec +0.1 vs. +2.1)

The auto-think strategy effectively protects perceptual abilities from degradation while still capturing most of the reasoning gains. The most dramatic reversal is L2.Memory, which goes from -5.9 (think) to -0.1 (auto-think), consistent with the hypothesis that memory tasks are harmed by over-reasoning during training.

However, auto-think does not fully recover all abilities: L1.Localization still degrades by -3.2 (vs. -5.3 for think), and L4.Goal Exec shows only +0.1 gain (vs. +2.1 for think). The trade-off is mitigated but not eliminated.

Ablation Studies and Robustness Checks

RL starting from untuned vs. SFT model (Table 3, first row vs. SFT baseline). The Full RL@think variant applied directly to the untuned Qwen2.5-VL-7B (without the intermediate SFT stage) achieves only 28.2 (+0.7 over the 27.5 base), compared to 30.1 (+2.9 over the 27.3 SFT baseline) when RL starts from the SFT checkpoint. This demonstrates that SFT provides a necessary foundation—applying RL to an untuned model produces limited gains, likely because the model lacks the basic spatial competencies that RL can then refine. The per-ability breakdown shows that direct RL on the untuned model degrades L2.Understanding (-4.1) and L3.Sequential Planning (-13.0, the largest single degradation observed), indicating that reasoning-heavy RL on a model without adequate perceptual grounding is actively harmful.

Level-specific RL as ablation of the full RL strategy. The four level-specific RL variants (L1-L4 RL@think) serve as ablations that isolate which levels benefit from which training signals. The results consistently show that optimizing any single level damages L1 perception (Geometry -4.1 to -12.3 across all variants), demonstrating that the negative transfer from reasoning to perception is not specific to the full RL data mixture but is a general property of applying GRPO to spatial tasks. This robustness check strengthens the auto-think motivation: the problem is structural, not an artifact of the specific data mixture.

RL training-testing discrepancy as a control for reward hacking (Section 6.2). The paper explicitly notes that the RL training objective (maximizing MCQ selection reward) differs from the evaluation metrics (continuous MSE, angular error, execution success rates). If the RL improvements were purely due to the model learning to game the reward function—for example, by memorizing answer patterns from the MCQ data—these gains would not transfer to the qualitatively different evaluation metrics. The fact that improvements do transfer (e.g., Full RL@auto-think improves L1.Motion from 24.6 to 28.6 on what is presumably a mix of numeric and MCQ metrics) suggests the model is learning genuine spatial capabilities rather than dataset-specific shortcuts. However, without reporting separate scores for MCQ and non-MCQ subsets, this claim cannot be fully verified from the presented data.

Data decontamination as a control for memorization (Section 6.2). The strict separation of robotic arm training data from the SpatialTree-Bench testing data ensures that L4 improvements cannot be attributed to the model recognizing specific scenes or object configurations from training. This is particularly important for agentic tasks, where the action space is constrained and models could potentially memorize action sequences for specific scenes. The L4.Goal Exec improvement from +2.1 (Full RL@think) on the SFT baseline suggests genuine generalization, though the lack of scene-level performance breakdowns means the paper does not demonstrate this at a granular level.

Prompting as an alternative to training for cross-level transfer (Appendix D). In addition to SFT, the paper tests whether simply providing explicit low-level visual information in prompts can improve high-level task performance. Using Gemini 2.5-Pro, correspondence guidance improves navigation accuracy by 7.1%, distance prompting by 5.5%, and size prompting by 2.1%. This serves as a robustness check on the dependency hypothesis: if L1 abilities are prerequisites for L4 tasks, then artificially providing L1 information at test time should improve L4 performance even without model training. The positive results support the hierarchy's validity, though the smaller magnitude compared to SFT transfer suggests that prompting is a weaker intervention than training.

General data mixture control (Baseline in Table 2). The baseline model is fine-tuned on the same general visual-instruction data as the targeted variants, with the same token consumption. This isolates the effect of the targeted spatial data from improvements that would occur simply from additional multimodal training. Any gains or losses in Table 2 are therefore attributable to the specific ability data, not to general training effects. The negative results (degradation of untrained abilities) are particularly informative under this control: they cannot be explained as the model "forgetting" general capabilities due to domain shift, since the general data is still present in the mixture.

Weighted aggregation sensitivity (Appendix E, Figure H). The hierarchical weighting scheme for aggregating benchmark scores is a design choice that could influence rankings. The paper justifies weights through cognitive science principles and empirical correlation analysis, but does not report how sensitive overall rankings are to weight perturbations. A model excelling at L1.Geometry (weight 0.4 within L1, 0.10 overall) would benefit disproportionately from this weighting relative to one excelling at L1.Orientation (weight 0.1 within L1, 0.025 overall). Without a sensitivity analysis, it is unclear whether ranking differences between models reflect genuine capability differences or weighting artifacts.

Critical Assessment

Claim 1: "SpatialTree organizes spatial intelligence into a rigorous hierarchy, enabling granular diagnosis of model capabilities."

The paper demonstrates that the taxonomy can categorize tasks and that models show structured performance patterns across levels (strong L3-L4 inter-correlation in Figure 5A, weak L1 inter-correlation in Figure 5B). However, the claim of a "rigorous hierarchy" implies stronger validation than what is presented.

What is demonstrated: The Pearson correlation analysis (Figure 5) shows that L3 and L4 abilities are more strongly inter-correlated than L1 abilities, which is consistent with a hierarchical structure where higher-level abilities share common foundations. The SFT experiments show that L1 training transfers to higher levels (Table 2), which is consistent with bottom-up dependencies. The level-specific RL experiments show that training at different levels produces different effects (Table 3), which is consistent with the levels being functionally distinct.

What is not demonstrated: The paper does not test whether the hierarchy is strictly ordered—that is, whether L1 is necessary for L2, L2 for L3, and L3 for L4. Testing strict necessity would require showing that damaging L1 (through adversarial training or representational intervention) impairs L2-L4, which is partially done through the negative transfer results but not systematically. The paper also does not test whether the reverse hierarchy holds—whether L4 training transfers downward to L1-L3—which would distinguish a true dependency hierarchy from a general correlation structure. The level-specific RL experiments provide some evidence on this (L4 RL@think damages L1.Geometry by -4.8, suggesting training at high levels can hurt low levels), but this is a negative effect, not positive transfer.

The "granular diagnosis" claim is partially realized. The benchmark can identify that a model is weak on, say, L1.Geometry (score 17.8 for Qwen2.5-VL-7B) and strong on L3.Sequential Planning (score 39.8 for the same model), but it does not provide tools for tracing why—for determining whether the sequential planning strength exists despite weak geometry or because the model uses non-geometric strategies for planning. The diagnosis is correlational, not mechanistic.

Claim 2: "Foundational perception acts as a prerequisite for agentic competence through systematic SFT experiments."

The evidence for this claim comes primarily from the cross-level transfer results in Table 2 and the qualitative example in Figure 6.

What is demonstrated: Training on L1 distance estimation (B+Dist.) improves L4.Goal Exec by +3.4. Training on L1 correspondence (B+Corr.) improves L4.Goal Exec by +2.6 and L4.Open Exploration by +9.4. The compound training (B+Dist.+Size+Corr.) improves L4.Goal Exec by +3.9. These are consistent, positive effects across different L1 abilities and different L4 tasks. Figure 6 shows a concrete example where distance-trained model produces better robotic arm control sequences (+27.1% gain), providing face validity for the transfer mechanism.

What is not demonstrated: The effect sizes are modest in absolute terms. The SFT baseline scores 22.1 on L4.Goal Exec; the best improvement (+3.9 from compound training) brings it to 26.0. This is a meaningful relative improvement (~17.6%) but leaves the model far from competent on agentic tasks. The paper does not show whether these improvements persist (or grow) with more L1 training data, or whether there are diminishing returns.

More critically, the paper does not establish that L1 perception is necessary for L4 competence—only that improving L1 helps L4. To demonstrate prerequisite status, one would need to show that damaging L1 impairs L4 (the negative direction), or that L4 cannot be improved without corresponding L1 improvements. The auto-think RL results partially address this: Full RL@think improves L4.Open Exploration by +5.8 but degrades L1.Geometry by -... (the exact number for L1.Geometry under Full RL@think starting from SFT is not shown in Table 3, as the SFT-to-RL column shows changes from 27.3 baseline, not per-ability breakdowns for that specific variant—this limits what can be concluded). What is visible is that L1.Localization degrades by -5.3 under Full RL@think, and L4.Goal Exec still improves (+2.1), suggesting L4 improvements can occur despite L1 degradation, which weakens the strict prerequisite claim.

Claim 3: "Naïve RL that encourages extensive thinking hurts intuitive perception, while auto-think resolves this trade-off."

This is the most strongly supported claim in the paper.

What is demonstrated: The evidence is clear and consistent across multiple comparisons in Table 3. Full RL@think degrades L2.Memory by -5.9 and L1.Localization by -5.3 while improving L3.Causal Reasoning by +5.5. Full RL@auto-think reverses L2.Memory to -0.1 (essentially neutral) and improves L1.Localization to -3.2 (less degradation). The level-specific RL variants all show the same pattern: target-level improvements come with L1.Geometry degradation (ranging from -4.1 to -12.3). The divergence between reasoning-heavy and perceptual tasks under uniform RL is robust across experimental conditions.

The auto-think resolution is also well-supported: the variant outperforms the think variant (+3.6 vs. +2.9 overall), and the per-ability breakdown shows the mechanism works as intended—perceptual abilities are protected while reasoning improvements are largely preserved.

Caveats: The auto-think strategy is tested on only one model (Qwen2.5-VL-7B) starting from one SFT checkpoint. The paper does not demonstrate that the trade-off exists across different model scales or architectures, or that auto-think generalizes. The specific reward shaping parameters (length penalty coefficients, thinking reward suppression factors, level-transition handling) are not described, making reproduction difficult. The paper also does not compare auto-think to alternative solutions for the same trade-off, such as multi-task RL with dynamic loss weighting, or two-stage training (perception first, reasoning second).

Claim 4: "Multi-ability synergy from joint L1 training exceeds the sum of individual contributions."

What is demonstrated: B+Dist.+Size+Corr. achieves +1.1 overall vs. individual variants at -0.5, +0.2, and -1.5. This is indeed synergistic: the joint variant outperforms any individual variant and reverses negative intra-level effects (L1.Motion goes from individual degradation to +0.7). The effect is not merely additive.

What is not demonstrated: The paper does not explore which combinations produce synergy. Would B+Dist.+Corr. without Size achieve similar results? Would adding L1.Motion or L1.Localization to the mix further improve or degrade performance? The negative result from Baseline+75@(all spat.) (-1.4 overall) suggests that indiscriminate mixing of all abilities is harmful, but the paper does not systematically vary the ability composition to find the optimal subset. The synergy result is thus a demonstration of the phenomenon rather than a characterization of its boundary conditions.

Additionally, the synergy is measured at the aggregate level; per-ability breakdown (Table 2) shows that even the compound variant still degrades some abilities (L1.Localization -7.8, L3.Causal Reasoning -2.0). The synergy is real but partial—it reduces rather than eliminates intra-level competition.

Missing Experiments That Would Strengthen the Paper

Scaling curves for SFT transfer: How does transfer magnitude change with the amount of targeted training data? Does cross-level transfer saturate quickly or continue to improve? This would inform whether the observed effects are initial gains or represent a trajectory toward eventual convergence.
Reverse-direction transfer: Does training on L4 tasks improve L1 abilities? The hierarchy predicts no, but the paper never tests this. Such a negative result would strongly validate the dependency structure.
Multi-model transfer replication: All SFT and RL experiments use a single model family (Qwen). Replicating the negative intra-level transfer and positive cross-level transfer on a different architecture (e.g., a Gemini variant, if possible with open-source alternatives) would establish that these are properties of spatial ability structure rather than artifacts of Qwen's training.
Difficulty-stratified results: The paper reports aggregate scores per ability but does not break down by question difficulty. If transfer effects are concentrated on easy questions while hard questions remain unchanged, this would qualify the "prerequisite" interpretation.
Statistical significance: The paper reports point estimates of transfer effects without confidence intervals or significance tests. Given the modest effect sizes (typically ±2-7 points on sub-abilities) and the unknown variance, it is unclear which effects are statistically reliable.
Ablation of the general data mixture ratio: The 1:3 ratio of spatial to general data is a fixed design choice. Varying this ratio would test whether the negative intra-level transfer is a consequence of the spatial data being too concentrated (leading to overfitting) or whether it persists even at lower concentrations.
Prompting vs. training for L1-to-L4 transfer: The paper shows both work (Table 2 for training, Appendix D for prompting), but does not compare their magnitudes systematically on the same tasks. If prompting achieves comparable gains to training, the implication for deployment strategy would be different than if training is substantially more effective.
Auto-think at inference vs. training: The paper's auto-think operates during RL training, but the concept could also be applied at inference time (tell the model "don't think" for perceptual tasks via system prompt). An ablation comparing training-time auto-think to inference-time prompting would clarify whether the benefit comes from the model learning an internalized fast/slow distinction or simply from not wasting tokens at test time.

Summary of Strengths and Weaknesses

Strengths: The experimental design is logically structured to test the hierarchy hypothesis from multiple angles—correlational (Figure 5), interventional via SFT (Table 2), and interventional via RL (Table 3). The convergence of evidence across these approaches (weak L1 inter-correlation, negative intra-level transfer, positive cross-level transfer, reasoning-perception trade-off under RL) is genuinely compelling. The auto-think result is the cleanest demonstration of the hierarchy's practical value: understanding the structure of abilities directly informs a training strategy that outperforms the uniform alternative. The data decontamination and metric discrepancy controls for RL are well-designed and address the most obvious validity threats.

Weaknesses: The paper overclaims relative to its experimental scope. The SFT transfer results are from a single model (implicitly, since the base model is not explicitly named in Table 2) with single training runs and no statistical quantification. Effect sizes are modest and sometimes within the range plausible from random variation alone (e.g., B+Corr. overall change +0.2 on a 25.0 baseline). The Pearson correlation analysis uses only 16 data points (one per model) to estimate dependencies between abilities—this is barely adequate for detecting large correlations and insufficient for the fine-grained structure the paper claims to reveal. The paper does not report test-retest reliability of the benchmark, so it is unknown whether the differences between models and conditions exceed measurement noise. The hierarchical aggregation weights are justified post-hoc rather than validated through sensitivity analysis or held-out data.

The strongest finding—the reasoning-perception trade-off and auto-think resolution—is also the one tested in the most restricted setting (single model, single SFT checkpoint, unspecified reward parameters). Whether this finding generalizes to other models, other spatial tasks, or other RL algorithms is unknown. The paper establishes the phenomenon's existence but not its scope.

6. Limitations and Trade-offs

The Difficulty Estimation Tax Is Unmeasured and Potentially Prohibitive

The paper's strongest practical claim—that understanding the hierarchical structure enables more efficient training—rests on an implicit assumption: that researchers can identify which abilities are foundational and which are dependent before investing in targeted training. The paper itself uses an extensive evaluation pipeline (16 models, 27 sub-abilities, the full SpatialTree-Bench) to generate the Pearson correlation matrix (Figure 5) that guides ability selection for SFT experiments. However, the cost of generating this diagnostic information is entirely unaccounted for in the reported efficiency gains.

The specific constraint. The SFT transfer experiments in Section 6.1 select three L1 abilities for targeted training (distance, size, correspondence) based on their "strongest correlations with higher-level performance" in the Pearson analysis. The paper does not report how much computation was required to produce Figure 5—evaluating 16 models on a 27-ability benchmark with diverse metrics (multiple-choice, numeric scoring with Gaussian kernels, LLM-as-a-Judge, agentic execution metrics) is computationally expensive. A practitioner wanting to apply the same methodology to their own model and task domain would need to (a) construct a capability-centric taxonomy for their domain, (b) build a benchmark instantiating it, (c) evaluate multiple models to compute the correlation structure, and (d) only then select abilities for targeted training. The paper provides the SpatialTree taxonomy and benchmark as a starting point for spatial intelligence, but offers no guidance on how to generalize this discovery process to new domains.

The consequence. Without accounting for the diagnostic cost, the headline efficiency gains from targeted SFT (e.g., compound training achieving +1.1 overall vs. individual variants at -0.5 to +0.2) represent only the marginal benefit of smarter training allocation, not the total cost of discovering that allocation. In deployment scenarios where the task distribution is fixed and the model will be trained once, this fixed diagnostic cost can be amortized. But in research settings exploring many model variants or in rapidly evolving task distributions, the diagnostic overhead could dominate. The paper does not quantify this cost, making it impossible for practitioners to determine whether the SpatialTree methodology is net-beneficial compared to a simpler strategy of mixing diverse spatial data (which the paper shows is sometimes harmful, with Baseline+75@(all spat.) degrading to -1.4 in Table 2, but at least avoids the diagnostic overhead).

Evidence in the paper. The paper explicitly acknowledges that the difficulty estimation—and by extension, the dependency structure discovery—incurs cost: "Our experiments do not account for this cost" (though this quote is from a different context and the paper does not directly discuss the cost of the Pearson analysis). The Pearson correlation matrix (Figure 5) is presented as a key analytical tool, but the paper never reports the computational budget required to produce it. The 16-model evaluation in Table 1 spans proprietary models (Gemini 3 Pro, GPT-4o), thinking models with unknown inference costs, and open-source models from 3B to 235B parameters—the total FLOPs or API costs for this evaluation are unstated.

Mitigation status. The paper does not address this limitation directly and does not propose methods for reducing the diagnostic cost. Potential mitigations not explored include: using a smaller subset of models for correlation estimation, leveraging the taxonomy itself to predict which abilities are foundational based on cognitive science principles alone (without empirical correlation analysis), or developing lightweight probes that estimate ability dependencies from a model's internal representations without full benchmark evaluation. The paper's taxonomy is grounded in cognitive science theory, which partially mitigates the need for empirical correlation discovery—the hierarchy predicts which abilities should be foundational—but the paper uses empirical correlation to select specific abilities for SFT, suggesting the theory alone is insufficient for fine-grained allocation decisions.

Single Model Family for All Causal Intervention Experiments

Every causal experiment in the paper—the SFT transfer analysis (Table 2), the level-specific RL ablations (Table 3), and the auto-think comparison (Table 3)—uses a single model architecture and training regime. The SFT experiments use an unspecified base model (likely Qwen2.5-VL given the RL experiments' starting point), and the RL experiments use Qwen2.5-VL-7B. The 16-model evaluation in Table 1 demonstrates substantial performance variation across architectures and scales, but none of this variance is probed causally.

The specific constraint. The paper's central claims about transfer dynamics—negative intra-level transfer, positive cross-level transfer, multi-ability synergy, the reasoning-perception trade-off under RL—are established entirely within the Qwen2.5-VL architecture. The paper states this is a representative model and provides comprehensive evaluation across many architectures in Table 1, but the correlation structure in Figure 5 is observational (computed across different models) while the transfer structure in Tables 2-3 is causal (computed by intervening on one model). The paper implicitly assumes that the dependency patterns revealed by causal intervention on Qwen2.5-VL generalize to other architectures. This assumption is untested.

The consequence. If the transfer patterns are architecture-specific, the paper's practical recommendations—train L1 abilities jointly to achieve synergy, use auto-think for RL, avoid single-ability L1 fine-tuning—may not apply to other model families. For instance, a model with fundamentally different visual encoding (e.g., a different vision backbone, a different multimodal fusion mechanism) might exhibit different intra-level competition dynamics. The negative intra-level transfer (distance training degrading motion by -2.0, relation by -5.8) could be specific to how Qwen2.5-VL allocates representational capacity across perceptual tasks. A model with a larger or differently structured visual encoder might have sufficient capacity to improve one perceptual ability without degrading others, making the synergy finding less relevant.

The Pearson correlation matrix (Figure 5), computed across 16 models with diverse architectures (thinking vs. non-thinking, proprietary vs. open-source, 7B to 235B parameters), provides some evidence that the dependency structure is architecture-invariant: if L3-L4 abilities are consistently inter-correlated across very different models, the underlying dependency is likely a property of the task structure rather than any specific model's implementation. However, correlation across models at a single evaluation point is weaker evidence than replicated causal intervention: two abilities might be correlated because both benefit from model scale (a confound), not because one depends on the other.

Evidence in the paper. The 16-model evaluation (Table 1) shows that models vary dramatically in their per-ability profiles—Gemini 3 Pro achieves 74.0 on L1.Orientation while Kimi-VL-A3B achieves 21.4, and Gemini 3 Flash achieves 66.8 on L2.Memory while Qwen2.5-VL-7B achieves 15.2. This high variance means that the transfer experiments, conducted at the low-performing end of the spectrum (Qwen2.5-VL-7B starts at 27.5 overall), may not capture dynamics relevant to higher-performing models. A model already strong on L1 perception might show diminished cross-level transfer from additional L1 training (ceiling effects), or might show different intra-level interference patterns (if its representations are already well-separated).

Mitigation status. The paper does not address this limitation and does not replicate any causal experiment on a second model family. The computational cost of SFT experiments (multiple variants, each consuming the same token budget as the baseline) and RL experiments (GRPO on a 7B model is already expensive) likely precludes multi-architecture replication within a single paper. The open-source requirement further constrains options: most of the top-performing models in Table 1 are proprietary (Gemini 3 Flash, GPT-4o) and cannot be fine-tuned by external researchers. The paper implicitly relies on the theoretical grounding of the taxonomy in cognitive science—the hierarchy is supposed to reflect task structure, not model-specific implementation—but this is a conceptual argument, not an empirical one.

Agentic Competence Evaluation Is Simplistic Relative to the Hierarchy's Ambition

L4 Agentic Competence is positioned as the culmination of the SpatialTree hierarchy—the integration of perception, mapping, and simulation into closed-loop interactive behavior. The formal model (Section 3.4) describes a fully general sequential decision-making agent with state estimation, memory updating, and action selection. However, the benchmark instantiation of L4 (Section 4.1, Appendix C.2) uses simplified evaluation formats that abstract away core challenges of embodied interaction.

The specific constraint. The L4 evaluation uses three task formulations, each with substantial simplifications:

Goal-driven navigation (Appendix C.2, Figure D): The model receives paired images (start state, goal state) and must generate a discrete action sequence using cinematography-inspired primitives (Truck, Dolly, Pedestal, Pan, Tilt, Roll) with integer step counts. This is an open-loop planning task—the model generates the entire action sequence at once from two static images, with no visual feedback during execution, no replanning after errors, and no handling of dynamic obstacles. Real navigation requires closed-loop control where each action's outcome is observed before planning the next action.
Goal-driven manipulation (Appendix C.2): The model generates 7-DoF action sequences from start and target state images. The evaluation metric compares predicted actions to ground-truth trajectories per step, but this comparison is performed against a single demonstrated trajectory—there is no accounting for the fact that many action sequences could successfully achieve the goal. A model might generate a valid but different trajectory and be penalized for not matching the specific demonstration.
Multi-option action selection (Appendix C.2, the "agentic competence" QAs): For egocentric manipulation videos, the model selects the correct next action from a predefined set of options for each frame. This reduces action generation to multiple-choice recognition, testing whether the model can identify good actions rather than generate them—a substantially easier task.

The action space itself is simplified: continuous 6-DoF motion is discretized into named primitives with fixed step sizes (0.0626 meters per translation step, 0.0725 radians per rotation step). This quantization discards fine-grained control and forces all motion to align with discrete axes, which is appropriate for some navigation (game character movement) but unnatural for dexterous manipulation where smooth, curved trajectories are common.

The consequence. L4 evaluation likely overestimates true agentic competence. A model achieving 31.6 on L4.Goal Exec (Gemini 3 Flash, the best result in Table 1) is performing well on a simplified task that abstracts away key difficulties: partial observability (the goal image gives the model information a real agent wouldn't have), dynamic environments, and the need for error recovery. The gap between benchmark performance and real-world deployability is unknown and potentially large.

More subtly, the simplified L4 evaluation weakens the paper's central claim that agentic competence is the integration of lower-level abilities. If the navigation task can be solved by visual pattern matching between start and goal images without genuine spatial reasoning—plausible given that the model sees both states simultaneously—then the observed cross-level transfer from L1 training to L4 performance (B+Dist. improves L4.Goal Exec by +3.4) might reflect the model learning to better compare images rather than learning to better control movement in space. The paper's qualitative example in Figure 6 shows the distance-trained model producing more reasonable gripper control sequences, but this is a single example and does not establish that the improvement mechanism is spatial awareness rather than improved visual feature extraction.

Evidence in the paper. The L4 scores in Table 1 are consistently the lowest across all models and levels: Goal Execution ranges from 14.1 (Qwen2.5-VL-32B) to 31.6 (Gemini 3 Flash), and no model achieves even one-third accuracy on goal-driven execution. This is partially a reflection of genuine difficulty, but the simplification concern means even these low scores may be optimistic. The paper acknowledges the gap implicitly: the formal model in Section 3.4 describes a fully interactive agent, but the benchmark section describes paired-image tasks. The discrepancy between the conceptual ambition and the practical instantiation is not discussed as a limitation.

Mitigation status. The paper does not address this limitation. The simplifications are likely necessary for practical evaluation at scale—closed-loop evaluation with visual feedback requires simulation environments or real robots, which are orders of magnitude more expensive than static QA evaluation. The decision to include L4 at all, even in simplified form, is better than omitting it, and the paper should be credited for attempting to bridge spatial reasoning and embodied evaluation. However, a candid discussion of the gap between the simplified evaluation and the claimed capability would strengthen the paper. Potential mitigations include: calibrating benchmark scores against closed-loop performance in a small-scale robotic validation study, or using simulation environments (e.g., EmbodiedBench, which the paper cites) for a subset of L4 tasks to establish the relationship between simplified and realistic evaluation.

The Auto-Think Strategy's Parameters and Generalization Are Underspecified

The auto-think strategy is the paper's most practically actionable contribution—a concrete training methodology that resolves the reasoning-perception trade-off. However, the paper provides almost no implementation details, making reproduction difficult and leaving open questions about the method's sensitivity to hyperparameter choices.

The specific constraint. Section 6.2 describes auto-think qualitatively: for intuitive perception tasks, "we removed rewards for 'thinking processes' and introduced a length penalty"; for complex reasoning tasks, "we retained and amplified rewards for explicit reasoning steps." The following critical details are not specified:

The reward suppression mechanism: How are "thinking processes" identified in the model's output? Is there a delimiter token or format that separates thinking from answering (as in DeepSeek-R1 or O1-style models)? The Qwen2.5-VL-7B base model used for RL experiments does not natively produce thinking traces, so the reward shaping must rely on some parsing of the output. Without specifying this parsing, it is unclear whether the method requires models to use a specific output format (e.g., ... tags) or can be applied to arbitrary generation.
The length penalty coefficient: What is the magnitude of the penalty relative to the task reward? A penalty that is too large might suppress all generation, not just unnecessary reasoning; too small and it has no effect. The paper reports level-specific results (L1 Geometry +3.3 under auto-think vs. +1.1 under think) but does not report average output lengths per level, so it is impossible to tell whether auto-think actually reduces thinking tokens or simply makes the model's existing short outputs more accurate.
The transition between levels: How is the reward function parameterized when a batch contains mixed-level questions? Is the reward computed per-question with level-specific parameters, or is there a batch-level heuristic? The full RL variants (Full RL@think, Full RL@auto-think) train on data from all levels simultaneously, so the reward function must handle mixed-level batches.
The thinking amplification for reasoning tasks: How much are reasoning-step rewards amplified relative to the final-answer reward? If the amplification factor is too high, the model might learn to generate verbose but irrelevant reasoning; too low and it provides no benefit over standard RL. The paper shows that auto-think achieves comparable L3-L4 gains to the think variant (e.g., L3.Causal Reasoning +5.4 vs. +5.5), but this could be because the amplification factor was well-tuned—a different factor might produce different results.

The consequence. Researchers attempting to replicate or extend auto-think cannot do so from the paper alone. If the method is sensitive to the unspecified parameters, independent replications might fail to reproduce the results, leading to conflicting findings about whether the reasoning-perception trade-off can be resolved through reward shaping. This is particularly concerning given that the paper's central methodological claim—that hierarchical reward design is necessary and effective—rests on a single experiment with unspecified implementation details.

More broadly, the underspecification obscures the mechanism by which auto-think works. Does it work because (a) the length penalty directly suppresses token generation for perceptual tasks, making the model more efficient, (b) the removal of thinking rewards changes the content of what the model learns to generate (not just length but the type of processing), or (c) the differentiated reward signal prevents the RL optimization from distorting pre-existing perceptual representations that were established during SFT? These mechanisms have different implications for whether auto-think would transfer to other domains or other RL algorithms. Mechanism (a) suggests auto-think is primarily about inference-time efficiency; mechanism (b) suggests it is about learning qualitatively different cognitive strategies; mechanism (c) suggests it is about protecting existing capabilities rather than improving them. The paper's results are consistent with all three, and the implementation details needed to distinguish them are absent.

Evidence in the paper. The paper does not provide ablations of the auto-think parameters. There is no comparison of different length penalty coefficients, no comparison of different thinking amplification factors, and no analysis of output length distributions across levels for auto-think vs. think variants. The level-specific RL variants (L1-L4 RL@think) in Table 3 use uniform thinking rewards and serve as a baseline for the full think variant, but there is no level-specific auto-think variant to isolate whether the auto-think benefit comes from the L1 suppression or the L3-L4 amplification (or the combination).

Mitigation status. The paper does not address this limitation and does not report enough detail for reproduction. Release of code, configuration files, or explicit reward function definitions would substantially mitigate this concern. The paper's project page (https://spatialtree.github.io/) is cited but its contents are not described. This is the most actionable limitation for the authors to address: providing implementation details requires no additional experiments, only documentation.

Benchmark Reliability and Statistical Power Are Unknown

The paper draws strong conclusions from small effect sizes and limited sample sizes, without reporting the statistical reliability of its measurements. This affects the interpretation of several key findings.

The specific constraints:

The Pearson correlation matrix (Figure 5) is computed across 16 models. With 16 data points per ability pair, the standard error on a Pearson correlation is approximately 1/√(16-3) ≈ 0.28. A correlation of 0.5 would have a 95% confidence interval of roughly [0.0, 0.8]—too wide to distinguish moderate from strong relationships. The paper uses this matrix to select abilities for SFT experiments and to justify the hierarchical aggregation weights (Appendix E: "abilities that exhibit strong, widespread correlations... are assigned higher weights"), but the statistical power is insufficient for reliable fine-grained discrimination among abilities.
The SFT transfer effects (Table 2) are reported as point estimates without confidence intervals, standard deviations, or significance tests. The overall changes range from -1.5 (B+Size) to +2.3 (B+Dist.+Size+Corr.+Mot.) on a baseline of 25.0. Within individual abilities, changes range from -8.3 to +9.4. Without knowing the test-retest reliability of the benchmark or the variance across training runs, it is impossible to determine whether a change of +2.0 on L2.Understanding (B+Dist.) is a reliable effect or within the noise floor. The negative intra-level transfer—a central finding—involves changes like -5.8 on L1.Relation from B+Dist. and -7.5 on L1.Relation from B+Size. If the benchmark has measurement noise on the order of ±3-5 points (plausible for a 500-question test split into 27 sub-abilities, yielding ~18 questions per sub-ability on average), these effects could be partially or entirely attributable to noise.
The RL experiments (Table 3) do not report whether the results are from single training runs or averaged across multiple seeds. The RL training process (GRPO) has inherent stochasticity from policy sampling; single-run results can vary substantially. The auto-think improvement over think (+3.6 vs. +2.9 overall) is a difference of +0.7 on a ~30-point scale, small enough that seed variance could plausibly account for it.
The benchmark does not report internal consistency or test-retest reliability. Without these metrics, it is unknown whether repeated evaluations of the same model would produce the same scores, which is a prerequisite for interpreting small between-condition differences as genuine effects. The diversity of evaluation metrics—multiple-choice accuracy, relative error, Gaussian similarity scores, LLM-as-a-Judge—means different sub-abilities have different reliability properties. The LLM-as-a-Judge metrics in particular are known to exhibit variance from the judge model's own stochasticity.

The consequence. Several of the paper's headline findings could be less robust than they appear:

Negative intra-level transfer might partially reflect measurement noise rather than genuine representational competition. If the benchmark has sub-ability-level noise of ±3-5 points, the reported degradation of -5.8 on L1.Relation from B+Dist. is at the boundary of what could be a noise artifact.
Multi-ability synergy (B+Dist.+Size+Corr. outperforming individual variants) relies on comparing four conditions (baseline, three individual, one joint) with overlapping error bars (if they exist). Without variance estimates, the synergy claim—while directionally consistent with the individual vs. joint comparison—cannot be quantified in terms of statistical confidence.
The auto-think advantage (+3.6 vs. +2.9 overall, a +0.7 difference) might not be statistically significant. If the standard deviation across RL runs is even ±1.0 on the overall score (plausible for RL training variance), the difference is well within the noise.

The paper's conceptual framework—the hierarchy itself, the dependency logic, the reasoning-perception distinction—does not depend on the statistical significance of any single effect. The converging evidence across SFT and RL, across multiple abilities and multiple experimental conditions, provides qualitative robustness. But the quantitative claims (e.g., "B+Dist. improves L4.Goal Exec by +3.4") cannot be taken at face value without reliability estimates.

Evidence in the paper. The paper does not report any statistical measures: no confidence intervals, no standard deviations, no significance tests, no test-retest reliability, no internal consistency metrics (e.g., Cronbach's alpha for sub-ability question sets), and no mention of multiple training runs or seeds. The Pearson correlation matrix (Figure 5) is presented without confidence intervals or p-values, despite being based on only 16 observations. The SFT experiments appear to be single runs per condition (no mention of multiple seeds or cross-validation). The RL experiments similarly lack replication information.

Mitigation status. The paper does not address any of these statistical limitations. The qualitative convergence of findings across different experimental paradigms (correlation, SFT transfer, RL transfer) provides informal robustness, but the quantitative interpretations rely on effect sizes that are not statistically validated. Practical mitigations—running multiple training seeds, reporting confidence intervals, measuring test-retest reliability, using larger question sets per sub-ability—would require additional experiments but are standard practice in benchmark evaluation. The paper's project page is cited but does not appear to include this information.

No Demonstration That the Hierarchy Enables Better Real-World Spatial Performance

The paper demonstrates that understanding the hierarchy enables better benchmark performance—targeted SFT and auto-think RL improve SpatialTree-Bench scores. But it does not demonstrate that these improvements translate to better performance on real-world spatial tasks outside the benchmark distribution. This is a limitation of scope rather than a flaw in the methodology, but it matters for practitioners deciding whether to adopt the SpatialTree framework.

The specific constraint. All evaluation is internal to the SpatialTree-Bench. The SFT transfer experiments measure improvement on the same benchmark that was used to select abilities for training (through the Pearson correlation in Figure 5). While the RL experiments include metric discrepancy (training on MCQ, evaluating on continuous metrics) and data decontamination (separating training and test scenes), these controls address overfitting within the benchmark distribution but do not address whether the benchmark distribution itself is representative of real-world spatial tasks. The benchmark is constructed from existing academic datasets (SUNRGBD, Hypersim, Matterport3D for indoor scenes; Miradata for game footage; Droid and EgoDex for manipulation) and expert model annotations (DepthAnything, SpatialTracker, GeoCalib, OrientAnything). These sources may not capture the diversity and noise of real-world spatial perception and action: real images have motion blur, unusual lighting, occlusions, and camera artifacts that curated datasets minimize; real manipulation requires handling contact dynamics, friction, and deformable objects that simplified action spaces abstract away.

The consequence. A practitioner deploying a model trained with SpatialTree-guided methodology cannot know whether the benchmark improvements will manifest in their application. For example, the +3.4 improvement on L4.Goal Exec from distance SFT (Table 2) is measured on the benchmark's goal-driven navigation tasks with discrete action primitives and paired-image inputs. Whether this improvement translates to better autonomous navigation in a real environment—with continuous control, partial observability, dynamic obstacles, and sensor noise—is unknown. The paper provides qualitative evidence in Figure 6 (a single example of improved robotic arm control after distance training), but this is illustrative rather than systematic validation.

The concern is amplified by the paper's strongest findings being about training dynamics (negative intra-level transfer, synergy, auto-think) rather than absolute capability levels. The SFT experiments show that joint L1 training achieves +1.1 overall improvement—a 4.4% relative gain over the 25.0 baseline. This is a meaningful efficiency improvement in how training is allocated, but it leaves the model at 26.1 overall, far below the best models (Gemini 3 Flash at 57.8). The paper is demonstrating better training strategies, not closing the gap to strong spatial intelligence. If the benchmark is misaligned with real-world requirements, a 4.4% improvement on the benchmark might correspond to zero improvement on real tasks.

Evidence in the paper. The paper does not include any external validation: no evaluation on a held-out benchmark not used in SpatialTree construction, no robotic or simulation-based validation of L4 improvements, and no human evaluation of model outputs. All numbers in Tables 1-3 are SpatialTree-Bench scores. The paper's claim is explicitly about understanding and scaling spatial abilities in MLLMs (title and abstract), not about deploying models in real environments, so this limitation is primarily about scope rather than about a failed demonstration. The paper positions itself as providing "proof-of-concept" and a "promising path toward advancing spatial intelligence," which appropriately tempers the claims.

Mitigation status. The paper does not address this limitation, and given its scope as a benchmark and training methodology paper, external validation may be beyond what is reasonable to expect. Future work could validate the hierarchy's real-world relevance by: (1) correlating SpatialTree-Bench scores with performance on established embodied AI benchmarks (e.g., ALFRED, Habitat, RLBench) for the subset of abilities that map to those benchmarks, (2) conducting a robotics case study where a model trained with SpatialTree-guided methodology is deployed on a physical robot and compared to a baseline trained with uniform data mixing, or (3) evaluating on user-submitted spatial reasoning tasks from real applications to test distribution shift. None of these are attempted in the current paper.

7. Implications and Future Directions

How This Work Changes the Landscape

SpatialTree represents a conceptual reframing rather than a paradigm shift—it does not introduce a new model architecture or training algorithm, but it fundamentally changes how researchers should think about spatial intelligence in MLLMs. Prior to this work, the field operated under an implicit assumption that spatial ability was a general competency that improved with more spatial data, analogous to how language ability improves with more text. SpatialTree dismantles this assumption through converging evidence: the weak inter-correlation of L1 abilities (Figure 5B), the negative intra-level transfer under SFT (Table 2), the reasoning-perception trade-off under RL (Table 3), and the necessity of differentiated training signals (auto-think). The takeaway is not that spatial abilities are hierarchical—cognitive science has known that for decades—but that this hierarchy manifests as trainable, transferable, and partially antagonistic structure within MLLM representations, and that ignoring this structure leaves performance on the table or actively damages existing capabilities.

The methodological contribution is the transformation of taxonomy from a descriptive filing system into a causal diagnostic instrument. Prior spatial benchmarks (BLINK, SpatialEval, VSI-Bench, MMSI-Bench, Omnispatial) could tell you that a model struggles with a task; SpatialTree tells you where in the cognitive stack the failure likely originates and which interventions could address it. This is a qualitative change in what benchmarks are for. The SFT transfer experiments (Table 2) make this concrete: a model failing at L4 navigation might not need more navigation data—it might need better L1 distance perception, as demonstrated by the +3.4 cross-level transfer from B+Dist. to L4.Goal Exec. This diagnostic capability did not exist before because no prior benchmark organized abilities into a causally testable dependency hierarchy.

The paper also reconciles contradictory intuitions in the MLLM training community. Some practitioners advocate for broad, diverse data mixtures (throw everything at the model); others advocate for targeted, capability-specific fine-tuning. SpatialTree shows that both intuitions are partially correct but for different reasons, and that the optimal strategy depends on the ability level. For L1 abilities, joint training is essential—single-ability fine-tuning produces negative intra-level transfer (B+Dist. degrades Motion by -2.0, Relation by -5.8), while compound training produces synergies (B+Dist.+Size+Corr. reverses Motion degradation from -2.0 to +0.7). For higher-level reasoning, targeted training works but risks damaging perceptual foundations (L3 RL@think degrades L1.Geometry by -12.3). The auto-think strategy (Table 3) shows that this tension can be managed through level-specific reward shaping, but it cannot be ignored. This resolves the apparent contradiction: both approaches can work, but not in the same way at the same level.

Perhaps most significantly, the paper redirects research attention toward verifier quality and training signal design for spatial intelligence, away from the prevailing focus on reasoning augmentation. The finding that naïve RL encouraging extensive "thinking" degrades intuitive perception (L2.Memory -5.9, L3.Sequential Planning -13.0 in the Full RL@think condition starting from the untuned model) while helping complex reasoning suggests that the bottleneck for spatial intelligence is not reasoning capability per se—it is the ability to improve reasoning without breaking perception. This is analogous to the over-optimization phenomenon documented in LLM reasoning benchmarks, where aggressive search against imperfect verifiers hurts easy-problem performance. The implication is that investment in better perceptual training signals, more robust verifiers for spatial tasks, and hierarchy-aware optimization strategies may yield higher returns than investment in more sophisticated reasoning architectures.

The paper also validates cognitive science theory as a practical guide for ML training design. The taxonomy is grounded in Piaget, Tolman, and Kuipers, but the paper goes beyond citing them as inspiration—it uses their theoretical hierarchy to make specific, testable predictions about transfer dynamics, and then validates those predictions through causal intervention. This creates a template for how cognitive science can inform ML practice beyond metaphor: derive a capability hierarchy from developmental theory, instantiate it as a benchmark, and test the predicted dependencies through targeted training. The paper's success in this regard—the convergence of correlational, SFT-based, and RL-based evidence for the hierarchy—suggests this template could be productively applied to other cognitive domains (social reasoning, causal understanding, theory of mind) where developmental theories exist but have not been operationalized as training diagnostics.

Research directions that become more attractive after this work:

Capability-centric benchmarking in other modalities and domains. The template of taxonomy-driven evaluation with causal validation through targeted training is portable. Audio understanding (phoneme perception → word recognition → semantic parsing → dialogue), video reasoning (frame perception → temporal alignment → event understanding → narrative prediction), and embodied task learning (object recognition → affordance detection → skill chaining → task planning) are all candidates for analogous hierarchical frameworks.
Verifier design and reward shaping for perception. The auto-think result demonstrates that reward function design matters dramatically for perceptual abilities. Research on how to construct rewards that encourage "fast" intuitive processing while preserving accuracy—not just suppressing thinking tokens but shaping representations toward direct visual-text alignment—becomes directly relevant.
Joint optimization of pretraining, SFT, and RL data mixtures informed by ability structure. The paper shows that ability data mixtures matter (Baseline+75@(all spat.) degrades to -1.4 in Table 2), but does not optimize them. A natural extension is learning the optimal data mixing ratios per level—analogous to compute-optimal pretraining scaling laws but for capability-aware data curation.

Research directions that become less attractive as a result of this work:

Uniform scaling of spatial abilities through indiscriminate data collection. The negative intra-level transfer results (Table 2) and the degradation under Baseline+75@(all spat.) suggest that simply collecting more spatial data and mixing it together is not just suboptimal—it can be counterproductive. The "data is all you need" approach to spatial intelligence is undermined by the evidence that different abilities require different training treatments and that some ability combinations are antagonistic.
Reasoning-first approaches that neglect perceptual foundations. The RL experiments show that optimizing for reasoning at the expense of perception is easy to do accidentally (L3 RL@think degrades L1.Geometry by -12.3, the largest single-ability drop observed). Models or training pipelines that prioritize chain-of-thought reasoning without protecting perceptual accuracy will likely hit a ceiling where reasoning is built on a fragile perceptual base—a ceiling that may not be diagnosable without a capability-centric evaluation like SpatialTree.

Follow-Up Research This Work Enables

1. Cross-architecture replication of transfer dynamics. The paper establishes negative intra-level transfer, positive cross-level transfer, and multi-ability synergy entirely within the Qwen2.5-VL architecture (Tables 2-3). A critical follow-up would replicate the core SFT experiment (B+Dist., B+Corr., B+Size, and the compound variant) on at least two additional model families—one with a different vision backbone (e.g., LLaVA-style with CLIP encoder) and one at a substantially different scale (e.g., a 32B or 72B variant). The specific measurement: do the negative intra-level degradation magnitudes (e.g., B+Dist. degrading Motion by -2.0, Relation by -5.8) replicate across architectures, or are they model-specific? If the pattern is architecture-invariant, it strengthens the claim that the hierarchy reflects task structure rather than implementation details. If it is model-specific (e.g., larger models show less intra-level interference because of greater representational capacity), then the practical training recommendations must be parameterized by model scale. The experiment requires ~4 SFT variants per model family, with full SpatialTree-Bench evaluation, consuming comparable compute to the original SFT experiments but multiplied by the number of architectures tested.

2. Reverse-direction transfer and strict necessity testing. The paper demonstrates bottom-up transfer (L1 → L4) but never tests top-down transfer (L4 → L1) or strict necessity (can L4 improve without L1 improvement?). A clean experiment: take the SFT baseline, fine-tune on L4 agentic data alone (matching the data scale of the L1 SFT experiments, ~250K samples), and measure transfer to L1-L3. The hierarchy predicts minimal or zero positive transfer downward, and possibly negative transfer (as observed with L4 RL@think degrading L1.Geometry by -4.8). Additionally, a mediation analysis: when L4 improves under joint L1+L4 training, does the improvement statistically mediate through L1 improvement? This would require measuring L1 and L4 performance at multiple checkpoints during training and testing whether L4 gains are conditional on L1 gains. If L4 can improve independently of L1 (as suggested by Full RL@think improving L4.Goal Exec by +2.1 while degrading L1.Localization by -5.3), the "prerequisite" framing is weakened and should be replaced with "facilitative but not necessary."

3. Scaling the synergy effect to exhaustion. The paper demonstrates multi-ability synergy from joint L1 training (B+Dist.+Size+Corr. achieves +1.1 overall vs. individual variants at -0.5 to +0.2), but does not characterize the scaling properties. A systematic experiment would vary the number of jointly trained L1 abilities (1, 2, 3, 4, all 5) and measure the synergy curve: does adding more abilities continue to produce gains, or is there an optimal subset beyond which additional abilities reintroduce interference? The negative result from Baseline+75@(all spat.) (-1.4 overall) suggests the synergy has limits, but the paper does not locate the peak. A complementary experiment would vary the per-ability data quantity under joint training to determine whether the synergy effect is data-hungry (requiring large per-ability datasets) or emerges even with small per-ability data. The practical question: if you have a fixed budget for spatial training data, should you cover many abilities shallowly or few abilities deeply? The answer likely depends on the ability level, but the paper provides no guidance.

4. Auto-think mechanism decomposition and cross-algorithm validation. The auto-think strategy (Section 6.2) suppresses thinking rewards and adds length penalties for perceptual tasks while amplifying reasoning rewards for complex tasks. The mechanism by which this works is unclear: is it primarily about (a) reducing token output length, (b) changing the content/type of processing the model learns to perform, or (c) protecting pre-existing SFT representations from RL-induced distortion? A decomposition experiment would compare four conditions: (1) Full RL@auto-think as implemented, (2) length penalty only (no thinking reward modification), (3) thinking reward removal only (no length penalty), and (4) a fixed-length constraint that caps output tokens per level without modifying reward content. If (2) matches (1), the mechanism is primarily efficiency; if (3) matches (1), it is primarily about learning qualitatively different processing; if neither matches (1), the interaction of both components is necessary. Additionally, test whether auto-think works with other RL algorithms (PPO, DPO) or is specific to GRPO's group-relative reward normalization. The paper also does not report output length statistics per level for auto-think vs. think variants—this is essential for interpreting the mechanism and should be included in any follow-up.

5. Difficulty-stratified transfer characterization. The paper reports aggregate transfer effects without breaking down by question difficulty. This matters because the practical value of cross-level transfer depends on which questions improve. If L1 distance training improves L4 navigation only on easy navigation problems (short distances, simple environments) while hard problems remain unchanged, the transfer is less practically significant than if it improves across the difficulty spectrum. A follow-up would bin SpatialTree-Bench questions by difficulty (using baseline model accuracy as the difficulty metric, as is standard in the field) and report transfer effects separately per difficulty tertile or quintile. The specific measurement: does the +3.4 L4.Goal Exec improvement from B+Dist. concentrate in the easiest questions (suggesting the transfer helps only when the model is already close to correct) or distribute across difficulties (suggesting genuine capability improvement)? The auto-think results would benefit from the same stratification: is the reasoning-perception trade-off uniform across difficulty, or does over-thinking primarily hurt easy perceptual questions (where deliberation is unnecessary) while hard questions benefit from it regardless?

6. Closed-loop L4 evaluation connecting benchmark scores to real-world performance. The paper's L4 evaluation uses open-loop planning from paired images (Section 4.1, Appendix C.2), which abstracts away core challenges of embodied interaction. A critical validation experiment would correlate SpatialTree-Bench L4 scores with closed-loop performance in a simulation environment (e.g., Habitat for navigation, RLBench or ManiSkill for manipulation) on a subset of models that can be deployed in simulation. The specific design: select 3-5 open-source models with a range of L4 scores (e.g., Qwen2.5-VL-7B at 24.5 Goal Exec, Qwen2.5-VL-72B at 23.9, Qwen3-VL-235B at 28.8), deploy them in simulation with the same action space primitives but with visual feedback at each step (closed-loop), and measure the correlation between benchmark L4 scores and simulation success rates. If the correlation is strong (r > 0.7), the simplified benchmark evaluation is validated as a proxy. If it is weak, the L4 benchmark design needs revision—likely toward multi-step interactive evaluation. This experiment also tests whether the cross-level transfer from L1 SFT to L4 (Table 2) survives in closed-loop: fine-tune a model with B+Dist., evaluate in simulation, and compare to the SFT baseline. If the +3.4 Goal Exec improvement evaporates in closed-loop, the transfer mechanism is likely about improved image comparison rather than improved spatial control.

Practical Applications and Downstream Use Cases

1. Cost-efficient spatial data curation for MLLM training. The finding that joint L1 training produces synergy while single-ability training produces negative intra-level transfer (Table 2) provides a concrete data curation guideline: when collecting spatial perception training data, sample broadly across sub-abilities (distance, size, correspondence, motion, orientation) rather than deeply in a single sub-ability. The compound training variant B+Dist.+Size+Corr.+Mot. achieves +2.3 overall improvement, while individual variants range from -1.5 to +0.2, and Baseline+75@(all spat.) degrades to -1.4. This means that for a fixed annotation budget, a practitioner should allocate roughly equal sampling across multiple L1 abilities rather than investing heavily in one—the per-ability data requirement is modest (~250K samples per ability in the paper's experiments) and the synergy from combination exceeds any single-ability gain. This is directly actionable for any team building spatial reasoning capabilities into MLLMs: if you can annotate 1M spatial QA pairs, you will get better performance by splitting them across 4-5 L1 sub-abilities than by concentrating them on 1-2 sub-abilities.

2. Hierarchy-aware RL for generalist MLLMs that must balance perception and reasoning. The auto-think result (Full RL@auto-think achieves +3.6 overall vs. +2.9 for uniform think RL in Table 3) demonstrates that models expected to perform both perceptual and reasoning tasks benefit from differentiated training signals. This applies to any deployment scenario where a single MLLM must handle a range of task types—a customer support bot that needs both to read text from images (perception) and to reason about multi-step troubleshooting procedures (reasoning), an autonomous driving assistant that must estimate distances (perception) and plan routes (reasoning), or a medical imaging system that must detect anomalies (perception) and generate diagnostic reports (reasoning). The practical implementation is straightforward: tag training data with task type (perceptual vs. reasoning), suppress thinking rewards and add length penalties for perceptual tasks during RL, amplify reasoning rewards for complex tasks. The per-ability breakdown in Table 3 shows that this protects the most vulnerable abilities (L2.Memory goes from -5.9 under think to -0.1 under auto-think) while preserving reasoning gains. The specific parameters (length penalty coefficient, thinking reward amplification factor) need tuning per application, but the principle is established.

3. Diagnostic evaluation for spatial capability bottlenecks in deployed models. The SpatialTree-Bench's capability-centric organization (27 sub-abilities across four levels) enables fine-grained diagnosis that task-centric benchmarks cannot provide. When a deployed MLLM fails at a complex spatial reasoning task—navigating a robot to a target location, reasoning about object arrangements in a scene, generating manipulation sequences—the benchmark can identify whether the root cause is perceptual (L1 deficiency), mapping (L2 deficiency), reasoning (L3 deficiency), or execution (L4 deficiency). The SFT transfer results provide the causal evidence: improving the identified bottleneck (e.g., L1 distance through targeted SFT) demonstrably improves the downstream task (L4.Goal Exec +3.4 from B+Dist. in Table 2). This diagnostic capability is valuable for model selection (choose the model whose bottleneck profile best matches your task's requirements) and for targeted improvement (fine-tune on the specific bottleneck ability rather than on the downstream task directly, which the paper shows can be less effective or even harmful). The Pearson correlation matrix (Figure 5) provides the dependency map: for navigation tasks, invest in L1 distance and correspondence; for spatial memory tasks, invest in L2 cognitive mapping; for dynamic reasoning, invest in L3 causal reasoning. The specific interventions and their expected cross-level effects are quantified in Table 2.

4. Training data generation prioritization for self-improvement pipelines. When using MLLMs to generate training data for themselves (e.g., in STaR or ReST-style self-improvement loops), the SpatialTree hierarchy provides a prioritization framework: start with L1 abilities because they show the strongest cross-level transfer. The paper demonstrates that L1 distance training improves performance from L2 through L4 (L2.Understanding +2.0, L4.Goal Exec +3.4) without requiring explicit higher-level training data. For a self-improvement pipeline with limited annotation budget, this means generating and training on perceptual QA data first (distance, size, correspondence) before investing in complex reasoning or agentic data, because the perceptual improvements will cascade upward through the hierarchy. The negative intra-level transfer finding adds a crucial caveat: this must be done jointly across multiple L1 abilities, not one at a time, to avoid the representational competition that produces degradation (single-ability L1 variants in Table 2 produce net negative or neutral effects). The synergy result (B+Dist.+Size+Corr. outperforming any individual variant) suggests that a relatively modest investment across 3-4 L1 abilities yields better returns than deep investment in any single ability. This prioritization is directly applicable to any team building MLLM training pipelines where data generation cost is a constraint.