acceptodds
Under review as a conference paper at ICLR 2027

IntentWAM: Task Intent as Context for Cross-Task Generalization in World-Action Models

Abstract

In-context learning from demonstrations offers a promising route to unseen robot tasks, but transferring demonstrated behavior across embodiments requires connecting task intent to the current execution scene. We propose IntentWAM, a world–action modeling framework with a unified conditioning interface that combines an Object-Centric Relational Task Specification (ORTS) with target-scene role bindings. ORTS encodes task roles, endpoint scene graphs, and object dynamics from both robot and human demonstrations. Combined with target-scene role bindings, ORTS provides intent tokens that guide visual-future prediction and subsequent action generation. Policy post-training associates demonstrations and robot executions by task identity, without requiring trajectory-specific demonstration construction or temporal correspondence between them; deployment uses external demonstrations as context without parameter updates. On seven held-out RoboTwin tasks, IntentWAM achieves mean success across robot and generated human demonstrations with a fixed UR5-WSG execution policy. With filmed human demonstrations from each evaluated layout, real-world evaluation after task-specific adaptation yields 47.50% success on held-out layouts, versus 22.50% for the strongest evaluated baseline.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Robot Learning, In-Context Learning, World–Action Models

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_DcNbOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

IntentWAM conditions world-action modeling on object-centric task intent. It extracts ORTS—task roles, endpoint scene graphs, and object dynamics—from robot or human demonstrations, grounds those roles to objects in the target scene, and encodes them as intent tokens that guide visual-future prediction and action generation. Its main contribution is a unified, embodiment-agnostic conditioning interface that allows one fixed policy to use same-robot, cross-robot, or human demonstrations via task-level demonstration–execution associations, without trajectory-specific pairing or temporal alignment. Validation includes held-out RoboTwin tasks under multiple demonstration sources and scene variations, real-world bimanual manipulation on held-out layouts, and component ablations, showing improved generalization over language-only and demonstration-conditioned baselines.

Critical strengths

One critical strength is the ORTS-based conditioning interface, which discards source actions and joint trajectories and represents demonstrations via task roles, endpoint scene graphs, and object motion, making the condition embodiment-agnostic. This is consequential because it allows one fixed execution policy to use same-robot, cross-robot, or human demonstrations through task-level associations, without trajectory-specific pairing or temporal alignment. A second strength is the validation across held-out RoboTwin tasks, multiple demonstration sources, scene perturbations, real-world held-out layouts, and component ablations, which substantiates that grounded object-level intent drives generalization over language-only and video-conditioned baselines.

Critical weaknesses

The critical weaknesese are listed as follows:

  1. Lack of causal isolation for the core interface. The comparisons against Zero-WAM and other baselines confound the ORTS/target-grounding interface with different checkpoints, source-specific fine-tuning, training mixtures, and additional fixed perception/language models. The component ablations are restricted to H demonstrations in standard UR5-WSG scenes, so they do not establish that the interface itself drives gains across R1/R2 or scene perturbations. This is consequential because the paper’s main claim is about the interface, not merely the full system.
  2. Real-world evidence is too limited and confounded. The real-world evaluation covers a single bimanual task/platform with very few trials per layout and no confidence intervals or significance tests. The cross-layout demonstration-reuse comparison is also confounded: the reused videos were seen during adaptation, while current-layout videos were not, so it does not cleanly isolate geometric generalization. This matters because held-out-layout real-world generalization is a central empirical pillar.
  3. Cross-embodiment claim is overstated. R2 source embodiments are already in the training pool, and execution is fixed to UR5-WSG; no new robot body is controlled zero-shot. Although source actions are discarded, controlling a new embodiment still requires that embodiment’s action data, channel mapping, normalization statistics, and adaptation/training. H also uses generated human videos rather than real human demonstrations. This is consequential because “embodiment-agnostic” applies mainly to the conditioning input, not to policy deployment, yet cross-embodiment transfer is a core claimed contribution.
Questions for authors
  1. Can you isolate the ORTS/grounding contribution with identical backbone, training data, checkpoint selection, and inputs?
  2. Can you report ORTS/grounding failure rates and decompose success by extraction, grounding, and execution failures?
  3. Can you clarify what exactly is required to deploy on a new embodiment not in the training pool?
  4. Can you provide confidence intervals/significance for the real-world results and a clean cross-layout demonstration-reuse control?
3 comments

Thanks for the careful review and constructive feedback, which helped strengthen our evaluation and clarify our claims. Our point-by-point responses follow:

Response to Q1.

We added matched controls sharing backbone initialization, execution training data, optimization, and the checkpoint-selection rule (Table 6, Appendix C.7). Full and matched raw video use identical demonstrations, language, robot observations, and task-level pairing. No demonstration retains instruction-derived grounded roles.

Ablation results (Table 6 of the revised manuscript).

\hline \text{Variant} & \text{Success (\\%)}\\,\uparrow & \text{Drop (pp)} \\\\ \hline \text{Full} & \mathbf{47.97} & \text{—} \\\\ \text{w/o OD} & 23.95 & 24.02 \\\\ \text{w/o TG} & 18.33 & 29.64 \\\\ \text{w/o IFP} & 32.14 & 15.83 \\\\ \text{Matched raw video} & 12.33 & 35.64 \\\\ \text{No demonstration} & 6.33 & 41.64 \\\\ \hline \end{array}$$ OD: object dynamics; TG: target grounding; IFP: future-chunk prediction. Under matched inputs and training, Full outperforms raw video (47.97% vs. 12.33%), while removing target grounding lowers success to 18.33%. These controls support structured demonstration conditioning and explicit target grounding. The evidence concerns the complete interface, including fixed perception. **Response to Q2.** We added a **300-rollout audit** across seven held-out tasks: 100 per source (R1, R2, and H; Table 8, Appendix C.9). R2 uses Franka-Panda demonstrations. Failed rollouts are classified hierarchically: extraction errors; missing, ambiguous, or incorrect required-role bindings after extraction passes; or execution failures after both checks pass. **Outcome decomposition.** $$\begin{array}{lcccc} \hline \text{Source} & \text{Task success (\\%)} & \text{Extraction failure (\\%)} & \text{Grounding failure (\\%)} & \text{Execution failure (\\%)} \\\\ \hline \text{R1} & 48 & 4 & 8 & 40 \\\\ \text{R2} & 46 & 3 & 10 & 41 \\\\ \text{H} & 45 & 7 & 6 & 42 \\\\ \hline \end{array}$$ Failures with detected extraction or grounding errors account for **12–13%** of rollouts, while **40–42%** fail after both checks pass, making execution the largest remaining failure category. These are outcome categories, not standalone module error rates. **Response to Q3.** We agree that the scope should be stated more precisely. Our **“embodiment-agnostic”** claim concerns the demonstration-conditioning interface: ORTS excludes source actions and joint trajectories. Deployment on a new execution robot still requires robot-specific action data, compatible observation inputs, action-channel mapping, normalization statistics, and policy training or adaptation. We do not claim zero-shot control of an unseen robot. In RoboTwin, execution is fixed to UR5-WSG, and R2 source embodiments are included in the training pool. Our results therefore demonstrate transfer across demonstration sources within this setting. H demonstrations in simulation are generated; our real-world experiments use filmed human demonstrations. **Response to Q4.** We added **two-sided 95% Wilson confidence intervals** for the new real-world evaluations. Scrambled-egg results appear in Table 5, with an additional Zero-WAM baseline in Appendix B.9. **Extended scrambled-egg evaluation.** $$\begin{array}{lcc} \hline \text{Method} & \text{Successes/trials (\\%)} & \text{95\\% CI (\\%)} \\\\ \hline \text{Full IntentWAM} & \mathbf{8/20\\;(40.0)} & \text{21.9–61.3} \\\\ \text{Matched raw video} & 1/20\\;(5.0) & \text{0.9–23.6} \\\\ \text{No demonstration} & 0/20\\;(0.0) & \text{0.0–16.1} \\\\ \text{Without relational edges} & 5/20\\;(25.0) & \text{11.2–46.9} \\\\ \text{Zero-WAM} & 3/20\\;(15.0) & \text{5.2–36.0} \\\\ \hline \end{array}$$ For cross-layout reuse, we added a control comparing current-layout demonstrations with newly recorded $L_1$ demonstrations, **both excluded from training, adaptation, and model selection**. Both conditions use the same frozen IntentWAM checkpoint and execution settings, with 10 fresh rollouts at each of $L_2$–$L_5$ (40 per condition). These trials are separate from the original reuse experiment (Table 4, Appendix B.8). **Cross-layout reuse with unseen demonstrations.** $$\begin{array}{lcc} \hline \text{Demonstration} & \text{Successes/trials (\\%)} & \text{95\\% CI (\\%)} \\\\ \hline \text{Current-layout} & 28/40\\;(70.0) & \text{54.6–81.9} \\\\ \text{Reused }L_1 & 18/40\\;(45.0) & \text{30.7–60.2} \\\\ \hline \end{array}$$ Reusing unseen $L_1$ demonstrations achieves **45.0%** success versus **70.0%** with current-layout demonstrations, an observed decrease of **25.0 percentage points**. This control removes the mismatch in demonstration training exposure and shows lower observed reliability for cross-layout reuse. Our revised discussion explicitly acknowledges this limitation.

Thank you for the detailed response and the new experiments. The matched controls, including the no demonstration and raw video variants, address my main concern on isolating the interface. The clean cross layout control and the narrowed embodiment claim also resolve my other concerns, so I will raise my score. Two minor points remain: please state which demonstration sources the matched controls cover, and note that the real world results rest on small trial counts.

Thank you for your careful review and constructive feedback. We will make both points more explicit in the revised manuscript.

1. Demonstration Sources. The matched controls in Table 6 are evaluated on the seven held-out RoboTwin tasks under standard scenes with UR5-WSG execution. Demonstration-conditioned variants use the same fixed generated human demonstration (H) per task, whereas the no-demonstration variant receives none. During training, demonstration-conditioned variants share the same demonstration-source mixture as Full (Appendix C.7). The R1/R2 results are separate system-level comparisons. We clarify this evaluation scope directly in the Table 6 caption.

2. Real-World Trial Counts. The main candle-lighting comparison uses 10 trials per method per layout, while the new cross-layout reuse control uses 10 trials per condition per held-out layout. Both experiments therefore include 40 trials across the four held-out layouts (L2–L5). The scrambled-egg evaluation uses 20 trials per method. We report these counts explicitly in the revised manuscript and candidly acknowledge in the Limitations section that the relatively small sample sizes and limited task coverage introduce uncertainty. Accordingly, we will characterize the real-world results as preliminary evidence under the evaluated conditions.

Reviewer_7QesOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies in-context adaptation of world-action models to unseen manipulation tasks from a single demonstration, when the demonstration embodiment and scene both differ from the execution setting. The authors note that existing demonstration-conditioned methods either warp demonstrated trajectories into the target scene or directly use raw demonstration videos as context, tying conditioning to the demonstrator's embodiment and viewpoint. The proposed IntentWAM extracts an Object-Centric Relational Task Specification (ORTS) from the demonstration, comprising task roles, initial and goal scene graphs, and object dynamics. Roles are grounded in the robot's initial observation. The specification and grounding results are jointly encoded into intent tokens to condition visual-future prediction, and actions are decoded from the predicted visual features. Post-training associates demonstrations and executions only by task identity and adds an auxiliary future chunk prediction loss. Experiments cover seven held-out RoboTwin 2.0 tasks with same-embodiment, cross-embodiment, and generated human demonstrations, three types of scene perturbations, a real-world bimanual candle-lighting task evaluated on held-out layouts, component ablations, and demonstration-goal switching tests.

Critical strengths
  1. The authors note that trajectory warping and raw video context both tie the conditioning signal to the demonstrator's embodiment and viewpoint. They instead propose grounded object-centric task intent as a shared interface, allowing robot and human demonstrations to enter the model through the same tokens.

  2. IntentWAM comprises role inference, initial and goal scene graph extraction, object dynamics summaries, target-scene role grounding, intent-token encoding, and an auxiliary future chunk prediction loss. Demonstrations and executions are paired only by task identity, allowing a single checkpoint to support both robot and human demonstrations.

  3. Under both robot-demonstration conditions, IntentWAM outperforms fine-tuned Zero-WAM on all seven held-out tasks and degrades less under layout, appearance, and distractor variations. Real-world experiments show transfer to held-out layouts after adaptation at a single layout. Ablation and goal-switching experiments also show that the components contribute and that the demonstrated goal affects execution.

  4. The benchmark version, baseline checkpoints, and hyperparameters are fixed, aggregation rules are explicitly described, and the paper itself identifies where the comparisons do not isolate the interface's contribution.

Critical weaknesses
  1. Different Zero-WAM training recipes and the official human checkpoint's partly unreleased training data confound interface attribution. Matched raw-video controls and trajectory-specific pairing variants are missing, leaving task-level sufficiency untested. In real-world comparisons, π0 and LingBot-VA receive no test demonstrations, while RICL uses another backbone and robot-only retrieval. The 25-percentage-point gap cannot be attributed to the interface.

  2. Both role inference and target grounding are conditioned on language instructions. The variant without target grounding achieves 18.33%, close to the 17.41% of the language-only baseline LingBot-VA. There is no control that uses no demonstrations and relies only on roles inferred from the instruction and grounded in the initial observation. The only direct evidence that demonstration content matters is the goal-switching test, but it covers a single task and achieves only 16.33% Goal success. It is therefore unclear how much of the gain actually requires demonstrations.

  3. Cross-embodiment demonstrators belong to the training pool. Generated human videos share robot-source cameras and scenes, likely explaining the nearly identical results. Real-world evidence covers one platform, one task adapted with 20 trajectories at one layout, and five layouts, testing only layout transfer. Zero-shot applies only to post-training, while backbone pretraining exposure remains unspecified.

  4. Substring and unique-match rules leave repeated-category objects unbound, as low Stack three blocks success suggests. Fixed-threshold 2D predicates omit containment despite placement tasks and Figure 2's inside relation. Target-object identification accuracy covers only training-task and web images. Missing held-out extraction and grounding failure rates hinder separating policy and heuristic errors.

Questions for authors
  1. Could the authors add two controls to the simulation study? The first would keep IntentWAM's backbone, data, task-level pairing, and update budget fixed, but condition on raw demonstration videos rather than intent tokens. The second would use no demonstrations and construct role tokens only from roles inferred from the instruction and grounded in the initial observation. Together, these would clarify how much of the gain comes from the interface and how much actually requires demonstrations.

  2. For each held-out task and demonstration source, what proportion of evaluation rollouts have missing or ambiguous role bindings? What is the success rate conditional on successful grounding? For tasks involving placement into containers, what do the actually extracted initial and goal graphs contain when the predicate set omits containment?

  3. All four methods in the real-world study are trained for 30,000 updates, but effective batch sizes range from 8 to 32 and learning rates differ by an order of magnitude, so the number of samples seen by each method differs by up to a factor of four. Could the authors report results with matched sample exposure or with the baselines' original training lengths, and evaluate a demonstration-conditioned baseline such as Zero-WAM on the same platform?

  4. Equations (1) and (5) condition the action branch on the full task condition, while the text states that the action branch attends only to language and video features, without attending to intent tokens. Which formulation is actually implemented?

  5. Please refer to the Weaknesses.

1 comment

Thanks for the careful review and constructive feedback. Our revisions and point-by-point responses follow:

Response to Q1.

We added both requested simulation controls with matched backbone initialization, robot training data, optimization, and sample exposure, retaining task-level pairing where applicable (Table 6, Appendix C.7). Matched raw video replaces the ORTS/grounding interface; No demonstration retains instruction-inferred roles grounded in the initial observation.

Ablation results.

\hline \text{Variant} & \text{Success (\\%)}\\,\uparrow & \text{Drop (pp)} \\\\ \hline \text{Full} & \mathbf{47.97} & \text{—} \\\\ \text{w/o OD} & 23.95 & 24.02 \\\\ \text{w/o TG} & 18.33 & 29.64 \\\\ \text{w/o IFP} & 32.14 & 15.83 \\\\ \text{Matched raw video} & 12.33 & 35.64 \\\\ \text{No demonstration} & 6.33 & 41.64 \\\\ \hline \end{array}$$ These results support the structured interface and the contribution of demonstrations beyond language and grounded roles. **Response to Q2.** In our simulation audit, missing or ambiguous object associations occurred in fewer than 14% (both extraction and grounding procedures) of rollouts. Most association failures involve small, task-irrelevant background objects. Leaving these objects unmatched does not affect the identification of task-relevant roles or the interpretation of the demonstrated goal. When all required task roles (Object&target) were correctly bound, task success was 48–50%. For container-placement tasks, the initial and goal graphs record visible objects, their image geometry and available states, and supported 2D relations, without an explicit `inside` predicate (Appendix A.2). The initial graph describes the pre-manipulation configuration, while the goal graph records the visible terminal configuration. Together with object-motion summaries, these provide placement context without explicitly verifying containment. Relations lacking geometric evidence remain unknown. Execution success is evaluated independently by the benchmark's task checker. **Extended scrambled-egg evaluation.** Four matched variants and an additional Zero-WAM baseline. CIs are two-sided 95% Wilson intervals. $$\begin{array}{lcc} \hline \text{Method} & \text{Successes/trials (\\%)} & \text{95\\% CI (\\%)} \\\\ \hline \text{Full IntentWAM} & \mathbf{8/20\\;(40.0)} & \text{21.9–61.3} \\\\ \text{Zero-WAM} & 3/20\\;(15.0) & \text{5.2–36.0} \\\\ \text{Matched raw video} & 1/20\\;(5.0) & \text{0.9–23.6} \\\\ \text{No demonstration} & 0/20\\;(0.0) & \text{0.0–16.1} \\\\ \text{Without relational edges} & 5/20\\;(25.0) & \text{11.2–46.9} \\\\ \hline \end{array}$$ **Response to Q3.** We retrained and re-evaluated all methods with a common effective batch size of 8 and 30,000 updates, keeping other settings unchanged to match sample exposure. The updated results preserve the original performance trend (Table 3, Appendix B.5). We also added Zero-WAM as a demonstration-conditioned baseline on the same Nero platform. On the unseen scrambled-egg task, Zero-WAM achieves **15.0%** success (3/20), compared with **40.0%** (8/20) for IntentWAM. The extended comparison is reported in Appendix B.9. **Response to Q4.** The implemented action branch does not directly attend to intent tokens $Z$. Instead, $Z$ conditions the video stream, whose features $F_{i+1}^v$ already incorporate demonstration information. The action branch then attends to these features together with robot history and language: $$p_\theta^a\\!\left( A_{i+1}^r \mid F_{i+1}^v,h_i^r,c_{\mathrm{lang}} \right).$$ Thus, changing the demonstration can change the video features and consequently the generated actions, even without direct action-branch attention to $Z$. Language is also supplied directly to the action branch. In the original Equations (1) and (5), conditioning on $c$ expressed this overall task dependence, rather than specifying direct attention inputs. We have made the feature-mediated pathway explicit in the revised Equation (5) and added a detailed explanation in Section 3.4. **Response to Q5.** Responses 1–4 detail the added controls, baseline evaluations, and implementation clarifications. Our task-generalization claims concern tasks excluded from our controlled training and adaptation. Source embodiments are seen during training, human demonstrations in simulation are generated, and upstream pretraining exposure remains unverified. Limited real-world coverage and dependence on pretrained perception and heuristic grounding remain limitations. Task-level association is demonstrated feasible, while its comparative effect against trajectory-specific pairing has not been isolated.
Reviewer_vPjeOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper presents IntentWAM, a method to use object-centric scene graph extracted from one in-context demonstration as task specification in WAM. The method utilize external computer vision segmentation and tracking models and certain hand-written rules to construct the scene graphs. The WAM architecture is based on Zero-WAM, while replacing the task instructions source from text and human video to the object-centric scene graph coming from human, the same robot embodiment, or heterogeneous robot embodiment executing the same task. The authors conducted simulation experiments studying their method’s in-context learning performance on held-out tasks, generalization behavior, and contributions from various design choices. They additionally validated the generalization behavior or their method on one real world task.

Critical strengths
  1. Well-motivated design choice. Zero shot or few shot transfer is known to be difficult for robot learning without large scale pretraining, and the authors provide a cost-efficient alternative via providing an object-centric structured in-context demonstration. The inductive bias from the structured demonstration is sensible and enables task level transfer between heterogeneous embodiments.

  2. Well-designed simulation experiments. The authors demonstrate promising results in simulation by designing task level and scene level generalization as well as ablations on various components. Improvements upon language-only conditioned baselines as well as Zero-WAM conditioned on text and human video demonstration show the benefit from the paper’s method.

Critical weaknesses
  1. Limited methodological novelty. The main difference between this paper and Zero-WAM is how in-context demonstration is provided (changed from learned embedding from text and human demo video to the object-centric structured representation). Although this is a meaningful design choice, the underlying WAM architecture and auxiliary future prediction supervision largely follow existing work. In addition, constructing the object-centric structured representation relies on external pretrained models and hand-designed rules, which limits the generalizability and scalability of this approach.
Questions for authors
  1. Will the authors consider additional real world experiments demonstrating heterogeneous conditioning transfer (e.g. task-level transfer to unseen real-world tasks)?

  2. Can the authors provide further ablation removing the relational graph structure in the object-centric in-context demonstration and thus justify the design choice of using the graph structure instead of simply providing the object information, role embeddings, and motion features without the graph structure?

  3. Will the authors consider comparing with additional learning for in-context learning baselines such as ICRT[1]?

[1] Letian Fu and Huang Huang and Gaurav Datta and Lawrence Yunliang Chen and William Chung-Ho Panitch and Fangchen Liu and Hui Li and Ken Goldberg. In-Context Imitation Learning via Next-Token Prediction. 2025 IEEE International Conference on Robotics and Automation (ICRA).

2 comments

Thank you for the careful review and constructive feedback, which have helped improve our manuscript. Our revisions and responses follow:

Matched scrambled-egg evaluation. CIs are two-sided 95% Wilson intervals.

\hline \text{Method} & \text{Successes/trials (\\%)} & \text{95\\% CI (\\%)} \\\\ \hline \text{Full IntentWAM} & \mathbf{8/20\\;(40.0)} & \text{21.9–61.3} \\\\ \text{Matched raw video} & 1/20\\;(5.0) & \text{0.9–23.6} \\\\ \text{No demonstration} & 0/20\\;(0.0) & \text{0.0–16.1} \\\\ \text{Without relational edges} & 5/20\\;(25.0) & \text{11.2–46.9} \\\\ \hline \end{array}$$ **Response to Q1.** We added an unseen real-world scrambled-egg task excluded from policy training and adaptation conducted in this work (Section 4.2.2, Appendix B.9). The frozen policy follows one complete filmed human demonstration without task-specific updates or intermediate guidance. Under matched backbone initialization and training settings, IntentWAM achieves **40.0% success**, compared with 5.0% using raw video and 0.0% without demonstration-derived conditioning. These results provide initial evidence of **task-level human-to-robot transfer** and the benefit of structured demonstration conditioning. Removing relational edges reduces success to 25.0%, suggesting an additional benefit from explicit object relations **Response to Q2.** We added an ablation that removes explicit relational edges and their graph-attention contributions while retaining object features, geometry, role embeddings, motion features, and target-scene grounding. The variant is trained and evaluated under matched settings. As shown in the table in our response to **Q1**, removing relational edges reduces success from **40.0% (8/20) to 25.0% (5/20)**. This provides preliminary support for explicit relational modeling beyond the retained object, role, and motion features, with uncertainty acknowledged given the 20 trials per variant. **Real-world layout generalization (%).** $$\begin{array}{lccccc} \hline \text{Layout} & \pi_0 & \text{LingBot-VA} & \text{RICL} & \text{ICRT} & \text{IntentWAM} \\\\ \hline \text{Seen }L_1 & 20.00 & 40.00 & 30.00 & 40.00 & \mathbf{70.00} \\\\ \text{Held-out }L_2\text{–}L_5 & 0.00 & 22.50 & 12.50 & 27.50 & \mathbf{47.50} \\\\ \hline \end{array}$$ **Response to Q3.** Following your suggestion, we added **ICRT** to the real-world candle-lighting comparison (Section 4.2.1, Table 3 of the revised manuscript). All methods use the same robot adaptation corpus of 400 auxiliary-task trajectories and 20 candle-lighting trajectories at $L_1$, with 30,000 training updates and fixed parameters during evaluation. On the held-out layouts, IntentWAM achieves **47.50%** success, exceeding ICRT's **27.50%** by **20.00 percentage points**. This comparison provides additional evidence for real-world layout generalization after task adaptation against an in-context learning baseline.
Reviewer_vPjeOpenReview ↗

Acknowledgment of Author Response

Thank you for providing additional experiments and ablations addressing my concerns. I have no further questions regarding the methodology and would like to maintain my rating of 3 (weak acceptance).

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

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