The first concern is that the gain from changing the training objective is actually pretty small. The full method improves success under unseen perturbations from 87.0% to 88.8%, but that combines failure examples, graded scores, and ranking training. When the authors keep supervised training the same and only replace binary collision-and-stability targets with graded scores, the gain is just 0.6 percentage points, plus 0.03 in average instruction-chain length. The jump in five-instruction completion from 77.6% to 84.8% is more convincing, but that comes from the full method. More seeds and paired confidence intervals would help show whether the smaller objective-level gains are reliable.
That also makes the cost question important. The method needs geometry, successful grasp annotations, generated candidates, physical explanations, supervised training, and another stage of ranking optimization. None of that automatically makes it too expensive, especially when the required assets already exist. But without a cost breakdown, it is hard to tell whether the improvement is worth it. The authors could report data-generation and training costs, then compare against alternatives using the same budget, such as more prediction training, longer supervised training, or more robot demonstrations.
The data pipeline may also be much easier to scale for grasping than for other tasks. The main corpus has 500,000 examples, and the largest experiment uses one million, but these are additional examples for an already pre-trained model. They do not replace its large foundation-model corpus. Generating perturbations around known grasps is fairly convenient; getting the geometry and reliable success annotations in the first place is the harder part. It would help to know how many distinct objects, scenes, and successful grasps are behind those examples. Testing with reconstructed geometry or less complete annotations would also show whether the approach works outside well-prepared datasets.
Another concern is what the score actually means. It measures distance to the nearest known successful grasp, rather than directly measuring physical success. The simulator results show a useful overall relationship, but they do not guarantee that nearby candidates are always ordered correctly. An unannotated valid grasp could get a low score, while a tiny change near a successful grasp could suddenly cause a collision. Since those subtle differences are exactly what the method wants to teach, the authors could examine where geometric scores disagree with simulator outcomes, especially among closely ranked candidates.
The paper also leaves some uncertainty about which part of the training really matters. Physical explanations help, but that does not necessarily mean the model is learning a faithful reasoning process; they could simply provide useful extra supervision. Likewise, ranking training adds both a new objective and more optimization. The shuffled-target experiment is useful, but it swaps explanations and scores together, so it only shows that mismatched supervision is harmful. Separately shuffling each component, testing explanation-first against score-first training, and comparing ranking training with an equal amount of continued supervised training would make the argument much clearer.
The broader transfer claim needs some care too. It is encouraging that grasp-assessment pre-training helps downstream placing, stacking, and instruction chains. But that does not show that the same data construction can directly assess those actions. Grasping is unusually convenient because a scene and a candidate pose can provide a lot of the information needed. Pushing or mid-trajectory decisions may require predicting future consequences. A second action class would be a useful next test, followed by a task where judging one pose is not enough.
Finally, everything is tested in simulation. The extra robot embodiments are encouraging, but they do not address real perception errors, friction changes, or unpredictable contact. A small controlled real-robot experiment would make the practical case much stronger. The low-demonstration result also deserves a closer look: the advantage grows to 6.9 percentage points, but that could reflect better representations, faster learning, or both. Learning curves and longer-training baselines would help distinguish those explanations. The idea is interesting; what is still missing is a clearer picture of how much the evaluation objective itself contributes, what it costs, and how well it survives outside this setup.
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