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Geometry Conditioning in an Embodied SLM: Training Controls and Robustness Diagnostics in a 0.8B Hybrid Model
Hao Li, Haofei Sun, Lin He
Intelligence
Status: succeeded | Model: Gemma-4-26B-A4B | Prompt: intel-v1 | Confidence: 93%
Last extracted: 9/10/2026, 2:21:37 AM
Summary
This study evaluates the impact of geometry conditioning on a 0.8B hybrid language model (Qwen3.5-0.8B) adapted for robotic manipulation via LoRA and gated delta networks (GDN). Using the LIBERO-Spatial benchmark, the authors compare various conditioning strategies, including token adapters, decay-gate geometry injection, and token clocks. Results indicate that correct geometric alignment during training does not reliably outperform shuffled geometry controls, and while relative-coordinate policies show robustness to frame relabeling, all tested visual policies fail significantly under physical object displacement. The findings suggest that coordinate invariance does not guarantee physical-layout generalization in small-scale adaptations.
Entities (9)
Relation Signals (10)
Qwen3.5-0.8B → usedin → LIBERO-Spatial
confidence 98% · We compare these routes in Qwen3.5-0.8B on LIBERO-Spatial
f0 → achievessuccessrate → 28.9%
confidence 95% · Conditioning recurrent decay gates on geometric increments yields 28.9% success
f0-shuffled → achievessuccessrate → 36.7%
confidence 95% · compared with 36.7% when those increments are shuffled during training
c0 → achievessuccessrate → 24.4%
confidence 95% · 24.4% without explicit object/goal geometry
b1 → achievessuccessrate → 11.1%
confidence 95% · Token-clock conditioning scores 11.1%
c2 → achievessuccessrate → 34.4%
confidence 95% · c2 (tokens, relative) 31/90 34.4
Qwen3.5-0.8B → contains → Gated Delta Network
confidence 95% · 3:1 ratio of gated-deltanet (GDN) layers to full-attention layers
visual policies → failsunder → physical object displacement
confidence 90% · all four tested visual policies fall to at most 3/20 after a 5 cm object displacement
relative-coordinate policy → →
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Abstract
Abstract:We study how physical-state inputs affect a 0.8B hybrid language model adapted for manipulation with 6.2M trainable parameters. Six conditions are trained on three LIBERO-Spatial tasks and evaluated over three seeds and 540 held-out rollouts. Conditioning recurrent decay gates on geometric increments yields 28.9% success, compared with 36.7% when those increments are shuffled during training and 24.4% without explicit object/goal geometry. Both geometry policies receive correct inputs at evaluation. A token adapter using the same increments scores 27.8%; differences vary across seeds and remain inconclusive. Token-clock conditioning scores 11.1%, including one seed that fails to converge. In separate robustness tests, a state-only relative-coordinate policy retains 7/10 success under frame relabeling, whereas all four tested visual policies fall to at most 3/20 after a 5 cm object displacement. These results show no reliable advantage from training-time geometric alignment under this recipe and illustrate the gap between coordinate invariance and physical-layout generalization. Episode records, seed-level analyses, and figure-generation code accompany the paper.
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- Source: https://arxiv.org/abs/2609.09213v1
- Canonical: https://arxiv.org/abs/2609.09213v1
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Geometry Conditioning in an Embodied SLM: Training Controls and Robustness Diagnostics in a 0.8B Hybrid Model Hao Li †thanks: Equal contribution. Email: thomasli114514@gmail.com Haofei Sun11footnotemark: 1 Email: humphreysun98@gmail.com Lin He †thanks: Corresponding author. Affiliation: University of Tennessee, Knoxville Email: lynnhe@utk.edu Abstract We study how physical-state inputs affect a 0.8B hybrid language model adapted for manipulation with 6.2M trainable parameters. Six conditions are trained on three LIBERO-Spatial tasks and evaluated over three seeds and 540 held-out rollouts. Conditioning recurrent decay gates on geometric increments yields 28.9% success, compared with 36.7% when those increments are shuffled during training and 24.4% without explicit object/goal geometry. Both geometry policies receive correct inputs at evaluation. A token adapter using the same increments scores 27.8%; differences vary across seeds and remain inconclusive. Token-clock conditioning scores 11.1%, including one seed that fails to converge. In separate robustness tests, a state-only relative-coordinate policy retains 7/10 success under frame relabeling, whereas all four tested visual policies fall to at most 3/20 after a 5 cm object displacement. These results show no reliable advantage from training-time geometric alignment under this recipe and illustrate the gap between coordinate invariance and physical-layout generalization. Episode records, seed-level analyses, and figure-generation code accompany the paper. 1 Introduction Small language models can be adapted into robot policies with only a few million trainable parameters. For hybrid backbones that combine attention with gated recurrence, geometry can enter through the input tokens or the recurrent decay gates. It is unclear whether either route helps a visual policy learn to manipulate objects, or whether apparent gains depend on the geometric signal being correctly aligned with the demonstrations. We compare these routes in Qwen3.5-0.8B on LIBERO-Spatial (Liu et al., 2023). The base weights are frozen; LoRA, an input projection, and an action head are trained. A token-MLP adapter (c1) and a decay-gate adapter (f0) receive the same six-dimensional geometric increments at nearly equal parameter budgets. A second token adapter (c2) receives richer relative-state features. Within the gate route, we compare correct geometry, geometry shuffled during training, and token clocks (Fig. 1). Correct geometry does not outperform shuffled training in the recorded rollouts, and the c1–f0 comparison is unresolved. The clock condition has lower success and one failed training seed. We examine these differences per seed and task, then test two kinds of robustness: relabeling coordinates without moving the scene, and physically displacing an object. Relative coordinates handle the first test, but the tested visual policies fail the second. The study identifies limits of geometry conditioning under a small adaptation budget and provides controls for interpreting its apparent benefits. Related work. Visual manipulation policies such as OpenVLA (Kim et al., 2024), OpenVLA-OFT (Kim et al., 2025), and ACT (Zhao et al., 2023) learn action predictions from demonstrations. MiniVLA (Belkhale and Sadigh, 2024) explores smaller language backbones, and BAKU (Haldar et al., 2024) studies efficient multi-task policies. RoboMamba (Liu et al., 2024) applies state-space models to robotic reasoning and manipulation; here we study a conditioning interface in gated delta networks (Yang et al., 2024). Related applications in built environments include architectural feature recognition (Zou et al., 2023) and language-guided robotic air-quality monitoring (He et al., 2025). Our experiments concern the lower-level problem of converting physical observations into manipulation actions. Noise injection in imitation learning (Laskey et al., 2017) suggests a possible regularization role for shuffled geometry. A separate line of work on personalized agents finds that updated stored state need not change generated behavior (Sun and He, 2026); in our setting, the corresponding empirical question is whether adding physical state changes closed-loop performance. 2 Setup: one frozen SLM, two pathways Figure 1: Geometry-conditioning routes. Conditions are trained separately: c0 omits the geometry branches; c1 and c2 add token features; f0 and f0-shuffled condition the GDN gates; b1 supplies clock channels to the gate adapter instead of geometry. Base weights are frozen. Blue modules, LoRA, and the orange gate adapter are trainable. Host and adaptation. We use the 0.8B hybrid LM (Qwen3.5-0.8B) with a 3:1 ratio of gated-deltanet (GDN) (Yang et al., 2024) layers to full-attention layers. Policies are trained by behavior cloning on LIBERO-Spatial with action chunking (Zhao et al., 2023) (K=8K=8), an L1 objective (Kim et al., 2025) with gripper-event proximity weighting, previous-action noise, frozen dual-camera vision features, and language conditioning. Trainable parameters are matched to within 0.25% across conditions (6.215M–6.230M; Table 1): LoRA (Hu et al., 2022) rank-16 on attention/QKV projections — GDN decay projections are deliberately excluded so that decay-gate conditioning remains exclusive to the conditions under study — plus a linear input projection and a 512-unit action head. Vision features are the frozen vision tower of the same checkpoint, mean-pooled to 768-d per camera (agent-view and wrist), concatenated and scaled by 0.22 into the input projection. Gate conditioning. Each of the 18 GDN layers computes a per-head decay logit at,ha_t,h from the hidden state. We add a scaled, tanh-squashed bias driven by a 6-d physical feature vector gtg_t (object and goal translation-increment norms divided by 0.5 m, rotation-increment angles divided by π, log(1+Δt/0.05s) (1+ t/0.05\,s), and an event-boundary flag; entries are zero where poses are invalid): at,h←at,h+λℓσ(Whgt+bh),σ=tanh,λℓ=0,bh=0 at initialization,a_t,h← a_t,h+ _ \,σ\! (W_hg_t+b_h ), σ= , _ =0,\ b_h=0 at initialization, (1) where λℓ _ is one trainable scalar per layer and W has a random initialization (standard deviation 0.02). The tanh term is bounded; the learned scalar is unconstrained. Thus the patch is an exact no-op at initialization (6⋅16+16+1=1136· 16+16+1=113 parameters per layer, 2,034 total). The clock control uses six normalized clock channels (three local and three global) with the same affine–tanh–scalar form and parameter count; the shuffled-training control permutes the valid timesteps of gtg_t within each episode with a fixed seed during training. Evaluation uses correct online geometry for both f0 and f0-shuffled; LoRA excludes the decay projections, so decay-gate conditioning exists only through Eq. (1). Table 1: Condition matrix. Content: none / relative geometry (14-d: object- and goal-relative translations and an invariant axis block) / 6-d invariant increments gtg_t / scrambled gtg_t / token clock. id pathway content role trainable c0 — no object/goal geometry baseline 6,215,224 c1 tokens same gtg_t via 6→ 2 MLP matched-input control 6,217,286 c2 tokens relative geometry (14-d concat) pathway A 6,229,560 f0 decay gate invariant increments gtg_t pathway B 6,217,258 f0-shuffled decay gate shuffled training gtg_t alignment control 6,217,258 b1 decay gate token clock content control 6,217,258 Matched-input pathway comparison. c1 embeds the same six-dimensional gtg_t used by f0 through a 6→ 2 linear layer and GELU, concatenated before the shared input projection. Its total trainable count differs from f0 by 28 parameters. The raw inputs match, but the token bottleneck and layerwise gate adapter transform them differently. c2 uses a separate 14-d state representation. Protocol. Three-task joint training (35 demos per task; split manifest with SHA-256 provenance), three seeds, evaluation on ten held-out initial states per task — 6×3×3×10=5406× 3× 3× 10=540 rollouts — with stage decomposition (reach/grasp/transport/place) recorded per episode. Training uses 3,000 optimizer steps and batch size 32. The baseline retains proprioceptive inputs, previous actions, and language as well as vision; “no geometry” means no explicit object/goal geometry, not an image-only policy. We report Wilson intervals and exact paired McNemar tests for descriptive comparisons over identical seed/task/initial-state keys. These intervals and p-values omit dependence from shared training seeds and repeated initial states. We additionally report per-cell outcomes and exploratory per-seed effect sizes, leave-one-seed-out ranges, and a sensitivity analysis excluding the near-floor task 8. The sensitivity analyses are exploratory; the historical ledger and analysis provenance are described in Appendix A. Training loss is only an optimization diagnostic. 3 Findings 3.1 Training-time alignment Table 2 summarizes the 540 held-out rollouts. Correct gate geometry (f0) scores 26/90, compared with 33/90 for shuffled training and 22/90 for c0. The f0–shuffled contrast is −7.8-7.8 percentage points (p; paired wins–losses 12–19, descriptive p=0.28p=0.28). Correct temporal alignment provides no clear benefit in this comparison. Both policies receive correct geometry at evaluation, so inference-time reliance on geometry remains untested. Matched-input pathways. The c1 token-MLP and f0 gate adapters receive the same gtg_t and score 25/90 versus 26/90. Their difference is −1.1-1.1 p (13–14, descriptive p=1.0p=1.0), with per-seed differences of −10.0-10.0, −6.7-6.7, and +13.3+13.3 p. The comparison is inconclusive, with a possible bottleneck from c1’s two-dimensional embedding. The token configuration c2 improves over c0 by 10.0 p (16–7, p=0.093p=0.093). The sample is too small to resolve this potentially useful effect. The c2–f0 difference is 5.6 p (15–10, p=0.42p=0.42); because c2 carries 14-d relative state and f0 carries 6-d increments, this contrast cannot identify a pathway effect. Shuffled training exceeds c0 by 12.2 p (18–7, p=0.043p=0.043, uncorrected); the nine cell-level signs are 6 wins, 1 tie, and 2 losses (descriptive sign-test p=0.289p=0.289). The cell-level result weakens the evidence for an improvement. Seed and task sensitivity. Table 3 reports exploratory sensitivity analyses. The f0–shuffled difference changes sign across seeds; omitting task 8 narrows it from −7.8-7.8 to −1.7-1.7 p. The effect is sensitive to both seed and task selection. The c2–c0 trend stays positive when any one seed is omitted, but one of three individual seeds favors c0. Shuffled training could provide a regularization effect, or both geometry variants could be limited by the training recipe; the present results do not distinguish these explanations. Table 2: Held-out success (3 seeds × 3 tasks × 10 episodes) and paired McNemar tests vs. c0 over identical initial states (exact seed/task/episode pairing; descriptive, see Sec. 2). †One b1 seed failed to converge (App. B); excluding it, b1 vs. c0 is 3–8, p=0.23p=0.23. condition success rate [Wilson interval] vs. baseline (wins–losses, p) f0-shuffled (training) 33/90 36.7 [27.4, 47.0] 18–7, 0.043 c2 (tokens, relative) 31/90 34.4 [25.4, 44.7] 16–7, 0.093 f0 (gate, correct) 26/90 28.9 [20.5, 39.0] 14–10, 0.541 c1 (tokens, MLP) 25/90 27.8 [19.6, 37.8] 12–9, 0.664 c0 (no geometry) 22/90 24.4 [16.7, 34.2] — b1 (gate, clock) 10/90 11.1 [6.1, 19.3] 3–15, 0.0075† Table 3: Exploratory success differences (percentage points). Each seed contains 30 rollouts per condition. Leave-one-seed-out (LOSO) ranges are sensitivity ranges, not confidence intervals. Task exclusion retains tasks 0/4. contrast seed 0 seed 1 seed 2 LOSO range without task 8 c1 −- f0 −10.0-10.0 −6.7-6.7 13.3 [−8.3-8.3, 3.3] −6.7-6.7 c2 −- c0 20.0 16.7 −6.7-6.7 [5.0, 18.3] 11.7 f0 −- shuffled −6.7-6.7 6.7 −23.3-23.3 [−15.0-15.0, 0.0] −1.7-1.7 f0 −- b1 36.7 16.7 0.0 [8.3, 26.7] 26.7 b1 −- c0 −23.3-23.3 −6.7-6.7 −10.0-10.0 [−16.7-16.7, −8.3-8.3] −20.0-20.0 3.2 Clock conditioning The correct-geometry gate scores 28.9%, compared with 11.1% for the clock gate (20–4, descriptive p=0.0015p=0.0015). Both use the decay-gate interface, but their inputs differ in semantics, scale, and temporal statistics; this is not a distribution-matched test of semantic content alone. One of three b1 seeds fails to converge (L1 loss 0.882, versus 0.262 and 0.258 for its siblings). We retain that seed in the primary outcome because optimization failure is relevant to adaptation reliability. Excluding seed 0 from both conditions, b1 scores 10/60 (16.7%) and c0 15/60 (25.0%): b1–c0 is 3–8, p=0.227p=0.227. The corresponding f0–b1 contrast is 9–4, p=0.267p=0.267. The pooled deficit therefore combines an optimization failure with smaller closed-loop differences among the remaining seeds. Reaching declines from 55.6% for c0 to 27.8% for b1 (Fig. 3). A plausible hypothesis is that demonstration time predicts task phase, encouraging a shortcut that fails when closed-loop timing drifts. Input scaling, optimization sensitivity, and other explanations remain possible. Gate-activation measurements and scale-matched controls would be needed to distinguish them. More seeds are needed to estimate the frequency of training failures. 3.3 Frame relabeling The frame experiment uses earlier state-only policies on task 0 and ten training initial states, not the held-out visual checkpoints in Table 2. A world-frame relabeling rotates the supplied poses by φ ; world-frame action translations are mapped back before simulator execution. The physical scene is unchanged. Relative pose features are invariant under a common rigid transform: (GTee)−1(GTobj)=Tee−1Tobj(GT_e)^-1(GT_obj)=T_e^-1T_obj. The relative features therefore remain unchanged without retraining. In the staged records supplied here, the absolute-coordinate policy scores 4/10, 0/10, and 0/10 at 0∘0 , 45∘45 , and 90∘90 ; its mean minimum end-effector–object distance rises from 0.047 to 0.107 and 0.371 m. The relative policy scores 7/10 at all three angles, with 100% reaching, grasping, and transport (Fig. 2). An absolute-coordinate MLP variant also fails at nonzero angles, but its 2/10 unrotated score makes it a weak capacity control. The absolute policies are sensitive to frame changes, although the experiment does not identify the mechanism of failure. Figure 2: State-only frame diagnostic on ten training initial states per angle. (a) Success; (b) mean minimum reaching distance; (c) stage rates pooled over 45∘45 and 90∘90 . Values are recomputed from the supplied staged records. Figure 3: Main-table stage rates across 90 episodes per condition. Reaching success is lower for b1 than for c0. 3.4 Physical object displacement We separately displace the manipulated object by 5 and 10 cm in the table plane, using a deterministic per-episode diagonal direction. Table 4 evaluates seed-0 visual checkpoints on tasks 0 and 4, with 20 held-out rollouts per condition and displacement. Unlike frame relabeling, this changes the physical task. The evaluations run on a second machine; its 0 cm control scores are reported alongside the shifted scores to provide a local reference. They differ from the original main-table evaluations, so we do not pool machines. All four tested policies have at most 3/20 success at 5 cm and 0/20 at 10 cm. Reaching falls from 70–85% at 0 cm to 15–55% at 5 cm and 5–10% at 10 cm. Geometry therefore does not prevent the observed collapse. Distance errors are consistent with poor adaptation to displaced targets, but minimum distances alone cannot distinguish layout memorization from other control failures. Thus frame invariance alone is insufficient to predict performance after physical displacement. Table 4: Physical layout shift (seed-0 checkpoints, tasks 0 and 4, 10 held-out episodes each): success / reach / mean minimum E–object distance. success /20 reach % min E–obj (m) condition 0 cm 5 cm 10 cm 0 cm 5 cm 10 cm 0 cm 5 cm 10 cm c0 (no geometry) 7 1 0 70 30 10 0.048 0.061 0.096 c2 (tokens) 12 1 0 80 50 5 0.054 0.069 0.102 f0 (gate) 12 1 0 70 15 10 0.056 0.075 0.099 f0-shuffled 15 3 0 85 55 5 0.050 0.062 0.094 4 Implications and limitations The shuffled-training control changes how the geometry result should be read: f0 improves over c0 in aggregate, but correct temporal alignment does not improve over shuffled training. A test-time gate knockout would answer the separate question of whether either trained policy relies on geometry. The clock result also depends on training reliability: its pooled deficit shrinks when the failed seed is excluded. Finally, the frame and displacement tests measure different properties and should be reported separately. Limitations. We evaluate one model, three tasks, and three training seeds in simulation. The 24.4% baseline and near-floor task 8 leave open the possibility that a stronger training recipe would reveal geometry benefits. The matched-input c1 adapter has a two-dimensional bottleneck; wider embeddings could change the pathway comparison. The frame test uses state-only checkpoints and training initial states, while the layout test covers one seed and two tasks. Closed-loop outcomes also vary across machines. We measure adaptation size, but not on-device latency, memory consumption, or energy. References Belkhale and Sadigh [2024] Suneel Belkhale and Dorsa Sadigh. Minivla: A better vla with a smaller footprint. Stanford SAIL Blog, 2024. Haldar et al. [2024] Siddhant Haldar, Zhuoran Peng, and Lerrel Pinto. Baku: An efficient transformer for multi-task policy learning. In NeurIPS, 2024. He et al. [2025] Lin He, Saravanan Kanagaratnam, Lorena A. Zanandreis, and Min Deng. LLM-driven robotic indoor air quality monitoring: Advances in natural language interaction and decision-making. In ICRA Workshop on Future of Construction: Safe, Reliable, and Precise Robots in Construction Environments, 2025. URL https://construction-robots.github.io/papers/85.pdf. Hu et al. [2022] Edward J. Hu, Yelong Shen, Phillip Wallis, Zeyuan Allen-Zhu, Yuanzhi Li, Shean Wang, Lu Wang, and Weizhu Chen. Lora: Low-rank adaptation of large language models. In ICLR, 2022. Kim et al. [2025] Moo Jin Kim, Chelsea Finn, and Percy Liang. Fine-tuning vision-language-action models: Optimizing speed and success. arXiv:2502.19645, 2025. Kim et al. [2024] Moo Jin Kim et al. Openvla: An open-source vision-language-action model. arXiv:2406.09246, 2024. Laskey et al. [2017] Michael Laskey, Jonathan Lee, Roy Fox, Anca Dragan, and Ken Goldberg. Dart: Noise injection for robust imitation learning. In CoRL, 2017. Liu et al. [2023] Bo Liu, Yifeng Zhu, Chongkai Gao, Yihao Feng, Qiang Liu, Yuke Zhu, and Peter Stone. Libero: Benchmarking knowledge transfer for lifelong robot learning. arXiv:2306.03310, 2023. Liu et al. [2024] Jiaming Liu et al. Robomamba: Efficient vision-language-action model for robotic reasoning and manipulation. arXiv:2406.04339, 2024. Sun and He [2026] Haofei Sun and Lin He. When memory updates but behavior does not: Repairing implicit stale dependencies in personalized agent responses. arXiv preprint arXiv:2608.01619, 2026. URL https://arxiv.org/abs/2608.01619. Yang et al. [2024] Songlin Yang, Jan Kautz, and Ali Hatamizadeh. Gated delta networks: Improving mamba2 with delta rule. arXiv:2412.06464, 2024. Zhao et al. [2023] Tony Z. Zhao, Vikash Kumar, Sergey Levine, and Chelsea Finn. Learning fine-grained bimanual manipulation with low-cost hardware. arXiv:2304.13705, 2023. Zou et al. [2023] Han Zou, Jing Ge, Ruichao Liu, and Lin He. Feature recognition of regional architecture forms based on machine learning: A case study of architecture heritage in hubei province, china. Sustainability, 15(4):3504, 2023. doi: 10.3390/su15043504. URL https://doi.org/10.3390/su15043504. Appendix A Reproducibility and analysis provenance The ancillary file supplementary.zip contains 540 main-table, 90 staged frame-relabeling, and 240 layout-shift episode records, the split manifest, and the historical experiment ledger. The script scripts/analyze.py recomputes success counts, descriptive Wilson intervals, paired tests, cell signs, per-seed and task-exclusion sensitivity analyses, stage rates, and frame/layout distance summaries. The optional --figures DIR argument regenerates the two rollout figures with Matplotlib. The architecture diagram is provided as editable TikZ source. Duplicate episode keys and incomplete main-table pairings cause an error. Training summaries provide the reported fit losses and parameter counts; these are distinct from rollout outcomes. The ledger is a chronological research record containing planned gates, protocol changes, and observations, not an immutable registration of the final manuscript. The present sensitivity analyses and revised interpretations were added after inspecting the outcomes. Earlier pooled statistics in the historical ledger are superseded by the executable analysis with exact seed/task/episode pairing. The current figures use the supplied staged records consistently; no cross-run selection is performed. Appendix B Training-fit table (optimization diagnostic only) Means ± sd over 3 seeds (L1): f0-shuffled 0.214±0.0190.214± 0.019; f0 0.217±0.0010.217± 0.001 (training-loss variability only); c1 0.256±0.0100.256± 0.010; c0 0.282±0.0870.282± 0.087; c2 0.295±0.0650.295± 0.065; b1 seeds 0.882,0.262,0.258\0.882,0.262,0.258\ — seed 0 failed to converge, and its closed-loop score (0/30) is reported both pooled and excluded in Sec. 3.2. Fit ordering is recipe-dependent and does not predict closed-loop success — another argument for closed-loop-first evaluation. Appendix C Per-cell success table Successes out of 10 held-out episodes per (seed, task) cell; tasks 0/4/8 of LIBERO-Spatial. seed 0 seed 1 seed 2 condition t0 t4 t8 t0 t4 t8 t0 t4 t8 total c0 3 4 0 7 0 0 8 0 0 22 c1 2 4 2 8 0 0 7 1 1 25 c2 6 5 2 4 8 0 6 0 0 31 f0 6 5 0 5 5 0 4 1 0 26 f0-shuffled 7 2 4 6 2 0 9 1 2 33 b1 0 0 0 5 0 0 3 2 0 10 Task 8 is near the floor for every condition; seed-to-seed variation within a condition (e.g. c2: 13/12/6 per seed) is of the same order as the between-condition differences in Table 2, which is why we treat the paired tests as descriptive. Appendix D Research practice and broader impacts Qwen3.5-0.8B is the policy backbone described in Sec. 2. AI coding assistants also supported experimental planning, implementation and debugging, analysis scripts, and manuscript preparation. The reported success rates are computed from recorded simulator outcomes; language-model judgments are not used to score rollouts. The revised analyses are identified as exploratory in Appendix A. The failure cases may help researchers avoid unsupported claims of spatial robustness in small robot policies. Deploying such policies on physical robots without further validation could cause collisions or property damage, particularly after scene changes. The experiments reported here are confined to simulation and do not establish safe physical deployment. No new human-subject study or crowdsourced annotation was conducted for these experiments. The supplement supports reanalysis of the recorded rollouts. It does not include a complete training/evaluation environment or the trained checkpoints, and a complete accounting of per-run and exploratory compute is unavailable. The model and benchmark are credited in the paper; a full dependency and asset-license inventory is not included in this submission.