Decision and Meta-Review
rejected
Decision note: Not accepted: its area chair recommended rejection.
Originality: checked, nothing found (Platform overlap: client.py similar on this submission (hashed-token abstract similarity + 8-gram overlap) against conference papers. Prior work outside the platform: read the originality sections of all five reviews and the AC's evidence references (CADTests, CAD-Coder, CAD-RL, GIFT, RAFT, ReST-EM, AWR, Casey et al. 2025 arXiv 2504.13178, 'The Verifier is the Curriculum' arXiv 2607.09709, LMBuild arXiv 2610.04292). I did not run lit_check.py myself; the external search is the reviewers' and the AC's, not mine.) — No platform paper is flagged suspected: the highest 8-gram text overlap is 0.002 and the closest abstract (a c2 CAD paper on face-local part programs) shares 0.001 of phrases. All five reviewers report no_concerns. Two uncited related works (Casey et al. 2025; arXiv 2607.09709) bear on novelty and positioning, not on copied text or results.
Language-model agents that build 3D structures must create functional parts by writing programs, and open models fail this step far more often than closed ones. A leading diagnosis holds that much of this gap comes from the tool's conventions, yet error counts cannot separate convention errors from geometric ones, and existing training rewards mix validity with closeness to a reference shape. We test by intervention a stronger reading of this diagnosis: that training toward valid programs suffices. PartSpec generates satisfiable functional and mating part specs scored by an exact, reference-free verifier on compiled solids, and Constraint-Margin Self-Training (CMST) self-trains a model on its own programs, weighted by a reward tilt. Two arms share initial weights, proposals and example counts, and differ only in the reward, constraint margins or validity alone, which both selects and weights the training examples. On 720 paired specs per model, the margin reward beats the validity reward on solved rate by 0.065 [0.044, 0.087] for Qwen3-1.7B and 0.050 [0.022, 0.075] for Llama 3.2 1B, positive in every seed, while validity-only training shows no reliable gain over imitation; for Llama, CMST itself does not beat imitation. Training toward valid programs is thus not sufficient for Qwen, whose validity-only arm does raise validity, once imitation has brought validity above 0.8; for Llama that arm lowers validity instead. Whether partial credit beats a binary solved reward is not tested. The pre-registered main claim also required the gain over imitation to be mostly spatial; that half fails, and no arm solves any spec of a held-out part archetype.
Figure 1. A geometric reward beats a validity reward at matched data, except on the held-out archetype. Qwen3-1.7B, solved rate per family-level cell (90 specs each). Bars are pooled means; the annotation above each CMST bar is its paired margin over validity-only self-training on the same specs. Both arms start from the same reference SFT weights and see the same proposals. The radar repeats the means on a shared scale. The cells are omitted because every arm solves none of them.
Introduction
Language-model agents now assemble 3D structures by retrieving parts, writing programs that create new ones, and placing them (Liu et al., 2026a; Pun et al., 2025; Son et al., 2026). Part creation is the step that decides whether the result works: a bracket needs its holes where the bolts go, a sleeve must clear its shaft, a peg must fill its socket. Text-to-CAD models write such parts as code, in CadQuery or constructive solid geometry (Khan et al., 2024; Xie et al., 2025; Guan et al., 2025; Rukhovich et al., 2025), and recent work trains them with reinforcement learning on geometric feedback (Guan et al., 2025; Niu et al., 2025; Gong et al., 2026; Giannone et al., 2026). Small open models are the ones a builder can fine-tune and run locally, and open models already trail closed ones at creating parts (Liu et al., 2026a); the 1–2B models we train are smaller still.
The LMBuild benchmark finds that open models fail the create-part step far more often than closed ones, finds that most failed calls break kernel conventions or program structure, and concludes that much of the gap stems from these rather than purely from spatial reasoning (Liu et al., 2026a). Its measure is whether a call executes, so the diagnosis concerns validity; it leaves open whether conventions also suffice for parts that meet their specification. If they do, the remedy is syntax: constrained decoding (Geng et al., 2024) or fine-tuning on any valid program. However, error counts cannot separate the two explanations, because a program that violates a convention never reaches the geometry check. Existing training signals do not separate them either. Rewards in CAD reinforcement learning bundle executability with closeness to one reference shape (Guan et al., 2025; Niu et al., 2025), so a gain cannot be credited to either, and a reference shape penalises any other part that would also work. Executable specification tests check function instead of resemblance, but they have been used for evaluation and test-time guidance (Mallis et al., 2026; Alrashedy et al., 2025), not as a controlled training signal.
We make the question answerable by intervention. PartSpec is a generator of functional and mating part specs in the LMBuild grammar, each satisfiable by construction and scored by an exact, reference-free verifier that probes the compiled solid with Boolean intersections. On top of it, Constraint-Margin Self-Training (CMST) is a one-round, reward-weighted self-training estimator (Zelikman et al., 2022; Gulcehre et al., 2023; Singh et al., 2024; Dong et al., 2023) whose weights are the tilt of a KL-regularised improvement (Peters et al., 2007; Peng et al., 2019). Two arms start from the same imitation weights and train on the same proposals and example counts, and differ only in the reward: partial-credit constraint margins for CMST, the validity gate for validity-only self-training. A Shapley split of constraint-level success into validity and conditional accuracy, and a fixed-population variant, then ask where any gain comes from.
On 720 paired training-family specs per model, the margin reward beats the validity reward for both Qwen3-1.7B and Llama 3.2 1B, by +0.065 [+0.044, +0.087] and +0.050 [+0.022, +0.075] in solved rate, with the sign positive in all three seeds of each (figure 1). Validity-only self-training shows no reliable gain over imitation for Qwen and is below it for Llama. Training toward valid programs is therefore not sufficient for Qwen, whose validity-only arm does raise validity, once imitation has brought validity above 0.8; for Llama that arm lowers validity instead. Whether the gain is mostly spatial is not settled: the pre-registered share test fails, and only post hoc views point to geometry for Qwen. No arm solves any spec of the held-out archetype, so this study shows no transfer to a unseen part type.
Our contributions are summarized as follows:
- PartSpec, a procedural benchmark of satisfiable functional and mating part specs with an exact, reference-free verifier that yields both a solved indicator and a partial-credit reward on compiled CSG solids (section 3).
- CMST, a reward-weighted self-training estimator derived from a KL-regularised reward tilt, in a design where the reward is the only treatment, acting through which examples are kept and how they are weighted; across two models, three seeds and 720 paired specs each, the margin reward beats the validity reward on solved rate (table 2), although for Llama both self-trained arms fall below imitation.
- A pre-registered syntax-versus-geometry decomposition of the gain, with a fixed-population correction, whose negative pre-registered verdict and post hoc readings we report side by side (table 3), together with a null on a held-out archetype that a floor limits: Qwen's arms rarely produce a valid solid there.
Related Work
Three lines of work meet in this study. Text- and image-to-CAD generation with language models writes sketch-and-extrude sequences or CAD code (Wu et al., 2021; Khan et al., 2024; Xie et al., 2025; Rukhovich et al., 2025), and the strongest recent systems add reinforcement learning on geometric feedback, such as Chamfer distance or intersection over union with a reference shape, usually summed with an executability reward (Guan et al., 2025; Niu et al., 2025; Gong et al., 2026; Giannone et al., 2026). A second line checks function instead of resemblance: executable specification tests (Mallis et al., 2026), vision-language self-verification (Alrashedy et al., 2025), implicit spatial constraints recovered by retrieval (Liu et al., 2026b), assembly-level mates (Dong et al., 2026; Wang et al., 2025), physical validity in brick worlds (Pun et al., 2025), and finite-element feedback for frontier agents (Son et al., 2026); these act at evaluation or inference time. The third line is reward-filtered and reward-weighted self-training for language models (Zelikman et al., 2022; Gulcehre et al., 2023; Singh et al., 2024; Dong et al., 2023), which descends from reward-weighted regression (Peters et al., 2007; Peng et al., 2019), and its online relatives built on proximal and group-relative policy optimisation (Schulman et al., 2017; Shao et al., 2024). Studies of what such training teaches report that outcome rewards generalise where imitation memorises (Chu et al., 2025), and that lint-only rewards for small code models shorten programs without functional gains (Skopin et al., 2026). Our study uses the third line's estimator with the second line's kind of check as the training reward, in the first line's setting, and makes the reward, through which examples are kept and how they are weighted, the only difference between arms. Unlike the reinforcement-learning CAD systems, it has no reference shape in the reward, so any part that meets the constraints counts as correct, and unlike the test-based checkers it changes the model's weights rather than its outputs at inference time. It also tests a validity-sufficiency hypothesis that the diagnosis in LMBuild motivates; which motivated this work but trained no model (Liu et al., 2026a). We provide a full discussion of related work in section 8.
Method
Figure 2. Constraint-Margin Self-Training on PartSpec. Row: a text spec enters, the policy writes a CSG program, an exact verifier scores the compiled solid, and CMST turns the scores into a weighted LoRA update; evaluation reports the greedy solved rate, paired by spec. (a): the verifier compiles the program, gates on a valid single-piece solid, and tests each constraint by Boolean intersection with probe solids, returning exact satisfaction and partial credit without any reference shape. (b): proposals sampled from the initial policy are ranked and weighted by the margin reward , filtered, and fitted by weighted likelihood. Every arm starts from the same reference SFT weights and trains on the same proposals and number of examples; only the reward that ranks and weights them changes.
Figure 2 shows the pipeline. Section 3 defines the PartSpec task, the exact verifier and the quantity we report. Section 3 derives CMST from a KL-regularised reward tilt and states the loss that ran, together with the validity-only self-training arm that differs from it only in the reward. Section 3 splits a gain into a syntactic and a spatial part, and section 3 gives the intervals.
Functional part specs and an exact verifier
A PartSpec spec is a triple : an object name, an optional fixed partner solid , and a list of geometric constraints . The policy , a base language model with a LoRA adapter (Hu et al., 2021), answers with a JSON program in the CSG grammar of the create-part tool of LMBuild (Liu et al., 2026a). The compiler evaluates with the manifold3d kernel and returns a closed 2-manifold solid, or on a parse, grammar or kernel error. Specs come in three families. Family (functional) asks for a single part from one of four archetypes (plate, hub, L-bracket, standoff board) with constraints on extent, through-holes, genus, mass, base area, bosses and symmetry. Family (mating) gives a partner body, a shaft or a plate with holes, and asks for a part that fits it: no interference, a coaxial bore inside a clearance band, a seat on a plane, pegs that fill the partner's holes, or a bounding box. Family holds out a fifth functional archetype, a channel, and is used only for evaluation. Complexity level sets the number of constraints . Each instance is cut from a hidden generator program that meets every chosen constraint, so every spec is satisfiable, yet the verifier never compares against that program.
The quantity we report is the population solved rate of a greedy policy. For an arm with trained parameters and a family , it is
where indexes the instance seed (which also seeds the training run of ), is the spec generator of family pooled over levels with equal weight, is greedy decoding, is the solved indicator defined next, and is the paired difference between two arms. Equation 1 is the object of every table: the headline is on .
The verifier turns a solid into three numbers. A gate requires a valid solid with one connected component. Each constraint returns an exact indicator and a partial credit that decreases with the size of the violation and equals 1 exactly when . Every predicate is a threshold on volumes of Boolean intersections with probe solids: a through-hole is a probe cylinder that must be empty together with wall material around it, no-interference bounds the volume shared with , and genus comes from the Euler characteristic of the mesh. From these,
where is the margin reward, the validity-only reward, and the solved indicator. Because if and only if , exactly when , so is an upper surrogate of that is tight at the top. Equation 2 is the only place where the two training arms differ: one optimises , the other , and both are scored by . Through the loss below, the reward decides both which proposals are kept and how they are weighted.
Constraint-Margin Self-Training
The target distribution. Reward-filtered self-training keeps the samples that pass a threshold (Zelikman et al., 2022; Gulcehre et al., 2023; Singh et al., 2024). A binary filter is sparse for small models on multi-constraint specs: on our self-training pools it keeps proposals for 22–27% of Qwen's specs and 40–44% of Llama's, against 80–94% for the margin threshold below. Whether that sparsity hurts is not tested here. A validity filter carries no geometry. We start from the KL-regularised improvement of the reward around the initial policy , whose maximiser is the reward tilt
where is the inverse temperature and the normaliser. This is the Gibbs variational identity behind reward-weighted regression (Peters et al., 2007) and advantage-weighted regression (Peng et al., 2019); it holds for any bounded reward, and equation 3 tells us which distribution the update should move toward.
Projection by weighted likelihood. Projecting onto the LoRA family with yields a likelihood weighted by under . With proposals , the self-normalised importance estimate is
where is the tilt weight of proposal within its spec. Equation 4 is consistent as ; with the small we can afford it is biased toward the proposals actually drawn, and we use it as the motivation for the loss that ran rather than as a guarantee.
The loss that ran. For each spec, CMST keeps the top- parseable proposals by among those with , then keeps the global top of these by ; call the result . The kept weights are not renormalised. Training minimises
where is the prompt length and the completion length in tokens, so the middle factor rescales the per-token mean to a per-sequence weight, and is a global constant that leaves the minimiser unchanged. Equation 5 departs from equation 4 in four ways: the threshold and top- cut drop the low-reward tail, the top- cut selects across specs, the length factor favours short completions, and two epochs of AdamW (Loshchilov et al., 2019) stop short of the argmin. These choices are shared by both arms, so they do not enter the contrast. We use , , , and , with LoRA rank 32 and one self-training round.
The validity-only arm. Replacing by in equation 3 gives
where the approximation leaves only a relative mass on invalid programs. Here every valid proposal of a spec gets the same weight, when of its proposals are valid, so the arm is rejection-sampling fine-tuning on the model's own valid programs, with less weight per example on specs where validity is easy. This is the trained form of a stronger reading of the LMBuild diagnosis (Liu et al., 2026a): that training toward valid programs is enough. In validity-only self-training the valid proposals per spec and the examples are drawn at random, whereas CMST ranks both by ; the contrast therefore covers both which examples are kept and how they are weighted.
Principle 1: Hold everything fixed except the reward, so that the reward is the treatment.
Both arms start from the same reference SFT weights , read the same proposals per spec, train on the same number of examples for the same number of epochs with the same LoRA seed, and are decoded with the same cap. The pooled solved rates are then not a comparison of training recipes but a paired test of one design choice, and equation 1 applied to the two arms on identical specs isolates it. The same rule fixes the initialisation: reference SFT imitates generator programs for the training families and is itself an arm, so the effect of self-training at all is measured against it.
Splitting a gain into syntax and geometry
The factorisation. A gain in solved rate could come from more programs that compile to one piece, or from better geometry among those that do. For a deterministic policy on specs, let be the fraction of constraints met by output when it passes the gate. Constraint-level success then factorises as
where is validity and is conditional constraint accuracy; the identity needs only . Equation 7 gives the two factors whose changes we attribute.
The pre-registered split. For policies we split by the two-factor Shapley rule (Shapley, 1953),
where and are the syntactic and spatial terms and is the spatial share. Expanding the right-hand side recovers , so equation 8 is an accounting identity. Before running the study we fixed the test: the gain of CMST over reference SFT is mostly spatial if the interval of lies above one half. The share is undefined when and unstable near it.
A fixed-population split. averages over the valid outputs, and that set changes when changes: if newly valid specs are harder, can fall while every previously valid spec improves. A spec-level partition by gate pattern avoids this,
where the three sums are the within-valid, gained-valid and lost-valid terms, and superscripts index the two policies. Only the within-valid term holds the population fixed, so it is the cleaner reading of geometric improvement. We added equation 9 and the reward contrast after the pre-registered test was evaluated; we report them as post hoc and they do not replace that test.
Estimation and intervals
Rates. Given the trained adapters, the solved count over specs is binomial, and we report the Wilson score interval (Wilson, 1927),
where is the population rate of equation 1, the observed rate and the two-sided 95% normal quantile. Unlike the Wald interval, equation 10 stays informative at , which is where the held-out archetype sits.
Paired differences. On identical specs, each pair of outcomes falls into one of four cells with probabilities , and the estimator satisfies, as in McNemar's test (McNemar, 1947),
where and count the specs that only the second or only the first arm solves. Equation 11 shows that precision is set by the discordant specs, not by alone. The intervals we print come from a paired percentile bootstrap (Efron, 1979) that resamples specs within each instance seed, and equation 11 serves as the normal-theory check on them. Both condition on the trained adapters. For variation across training runs we report the three per-seed paired differences, each from separately trained adapters on separate specs, and, as pre-registered, their interval with two degrees of freedom.
Experiments
We first report absolute solved rates for every arm and family in section 4, then test the reward contrast on paired specs in section 4. Section 4 asks where the gain goes, and section 4 examines the held-out archetype and the model-free floors. Finally, we remove one ingredient at a time across complexity levels in section 4.
Main results: solved rates across families
Evaluation Setup. We train Qwen3-1.7B in non-thinking mode (Yang et al., 2025) and Llama 3.2 1B Instruct (Grattafiori et al., 2024). For each of 3 instance seeds, every family-level cell holds 30 fresh evaluation specs, so a cell pools 90 specs, a family 360, and the training families 720. Each seed trains its own reference SFT adapter by imitation, and its own validity-only self-training and CMST adapters from a 300-spec self-training pool. Outputs are decoded greedily with a 2048-token cap using vLLM (Kwon et al., 2023). Two model-free floors anchor the scale: the box floor answers every spec with the same box, and the nearest-program floor returns the training program of the most similar spec. The whole sweep, 288 per-seed cells of 30 specs, used 3.812 GPU-hours on four 16 GB V100 cards. We introduce the row families of table 1 here: floors, comparison arms and CMST.
Results.
Table 1. Solved rate () by family. Rows: model-free floors, the two comparison arms, CMST. Each cell is the pooled solved rate over 3 instance seeds (360 specs per family, 720 for ) with its 95% Wilson interval in brackets. is the held-out archetype, never seen in training.
| (functional) | (mating) | (held out) | ||
|---|---|---|---|---|
| box floor (fixed box) | 0.000 [0.000, 0.011] | 0.000 [0.000, 0.011] | 0.000 [0.000, 0.011] | 0.000 [0.000, 0.005] |
| nearest-program floor | 0.025 [0.013, 0.047] | 0.097 [0.071, 0.132] | 0.000 [0.000, 0.011] | 0.061 [0.046, 0.081] |
| Qwen3-1.7B | ||||
| reference SFT | 0.156 [0.122, 0.197] | 0.400 [0.351, 0.451] | 0.000 [0.000, 0.011] | 0.278 [0.246, 0.312] |
| validity-only self-training | 0.142 [0.109, 0.181] | 0.442 [0.391, 0.493] | 0.000 [0.000, 0.011] | 0.292 [0.260, 0.326] |
| CMST (ours) | 0.175 [0.139, 0.218] | 0.539 [0.487, 0.590] | 0.000 [0.000, 0.011] | 0.357 [0.323, 0.393] |
| Llama 3.2 1B | ||||
| reference SFT | 0.108 [0.080, 0.145] | 0.650 [0.599, 0.697] | 0.000 [0.000, 0.011] | 0.379 [0.344, 0.415] |
| validity-only self-training | 0.031 [0.017, 0.054] | 0.578 [0.526, 0.628] | 0.000 [0.000, 0.011] | 0.304 [0.272, 0.339] |
| CMST (ours) | 0.056 [0.036, 0.084] | 0.653 [0.602, 0.700] | 0.000 [0.000, 0.011] | 0.354 [0.320, 0.390] |
Table 1 shows that CMST has the highest solved rate of the three Qwen arms, 0.357 [0.323, 0.393] against 0.292 for validity-only self-training and 0.278 for reference SFT, and that every model arm sits far above both floors on . Every model arm solves mating specs more often than functional ones. For Llama the ordering differs: CMST and reference SFT are close on , and validity-only self-training falls below both, mostly on , where it drops to 0.031. The two models also differ in what imitation already gives them. Llama's reference SFT is the stronger starting point on , and on both of its self-trained arms fall below it; a likely but untested explanation is that training on its own weaker programs moves the policy away from the generator programs it imitated. Qwen starts lower on and gains most there. These absolute rates set the scale for the paired contrasts that follow, but they are not the test: two arms with overlapping Wilson intervals can still differ reliably on the same specs, because most specs are solved by both or by neither.
The reward contrast on paired specs
Evaluation Setup. Each difference in table 2 is from equation 11 on identical specs, with a paired bootstrap interval stratified by seed. The pre-registered success rule for the reward contrast was an interval above zero for both models. It is the first half of the pre-registered main claim; the second half, that the gain over reference SFT is mostly spatial, fails (table 3), so that claim as pre-registered is not supported; only its first conjunct holds.
Results.
Table 2. Paired differences in solved rate ( favours the first arm). Each difference is taken on identical evaluation specs. Brackets are 95% paired percentile bootstrap intervals (2000 resamples, stratified by instance seed). "Seeds" counts the instance seeds whose difference is positive; "Disc." gives the discordant spec counts (first arm solves only / second arm solves only) on .
| Contrast | () | () | () | Seeds | Disc. |
|---|---|---|---|---|---|
| Qwen3-1.7B | |||||
| CMST validity-only self-training | +0.033 [+0.014, +0.056] | +0.097 [+0.058, +0.133] | +0.065 [+0.044, +0.087] | 3/3 | 57/10 |
| CMST reference SFT | +0.019 [-0.006, +0.047] | +0.139 [+0.094, +0.183] | +0.079 [+0.054, +0.104] | 3/3 | 76/19 |
| validity-only self-training reference SFT | -0.014 [-0.042, +0.011] | +0.042 [0.000, +0.086] | +0.014 [-0.011, +0.039] | 2/3 | 48/38 |
| Llama 3.2 1B | |||||
| CMST validity-only self-training | +0.025 [0.000, +0.050] | +0.075 [+0.028, +0.119] | +0.050 [+0.022, +0.075] | 3/3 | 66/30 |
| CMST reference SFT | -0.053 [-0.081, -0.025] | +0.003 [-0.042, +0.047] | -0.025 [-0.053, +0.001] | 0/3 | 39/57 |
| validity-only self-training reference SFT | -0.078 [-0.108, -0.047] | -0.072 [-0.119, -0.025] | -0.075 [-0.103, -0.049] | 0/3 | 29/83 |
The margin reward wins at matched data for both models (table 2). On , CMST minus validity-only self-training is +0.065 [+0.044, +0.087] for Qwen3-1.7B and +0.050 [+0.022, +0.075] for Llama 3.2 1B, positive in all three seeds for both, with 57 against 10 and 66 against 30 discordant specs. The interval stays above zero when any single family-level cell is dropped; the lowest lower bound is 0.021 for Qwen (without -L1) and 0.010 for Llama (without -L3). Across training runs, the per-seed differences are +0.062, +0.083 and +0.050 for Qwen and +0.042, +0.038 and +0.071 for Llama. The pre-registered seed-level interval (df ), which covers retraining and spec sampling together, is [+0.023, +0.107] for Qwen and [+0.005, +0.095] for Llama. Against reference SFT the picture splits by model. Qwen gains +0.079 [+0.054, +0.104], but its per-seed differences (+0.104, +0.092, +0.042) spread widely, with a seed-level interval of [-0.003, +0.161], so with three training runs the gain over imitation is reliable for these adapters but not shown to survive retraining; meanwhile Llama's difference of [, +0.001] includes zero and is negative on . Validity-only self-training shows no reliable gain over reference SFT on : its interval contains zero for Qwen and lies below zero for Llama. On it raises Qwen's gate rate over reference SFT from 0.829 to 0.876 but lowers Llama's from 0.860 to 0.828 (CMST: 0.903 and 0.863). For Qwen the arm does move validity: its syntactic term over reference SFT is +0.027 [+0.014, +0.042]. Imitation already brings validity above 0.8, far above the create-part success LMBuild reports for open models, so the arm tests training toward validity only in this high-validity regime. For Llama it does not even raise validity, so the cleaner evidence on sufficiency is Qwen's, where validity rises without a reliable gain in solved rate.
The contrast measures the reward acting through two channels at once. CMST ranks proposals by when it keeps the top per spec and the top overall, and it weights the kept examples by , whereas validity-only self-training keeps valid proposals at random with equal weights. Everything else in equation 5 is shared; separating selection from weighting would need an arm this study did not run. Selection changes the training sets: across seeds, 47–54% of the CMST examples for Llama solve their spec against 25–29% for validity-only self-training (Qwen: 22–25% against 11–13%). A filter on the solved indicator alone would also enrich the set, and the binary-reward arm that would test whether partial credit adds anything beyond it was not run. With , a solved example outweighs one at the threshold of the same spec by the factor , so the kept weights act close to a solved filter. The result is that a geometric reward beats a validity reward, not that partial credit beats a binary geometric reward. Since is an upper surrogate of , that ranking by enriches solved examples is expected; what the contrast adds is that this enrichment carries over to fresh specs after one round, whereas ranking by validity alone does not.
Where the gain goes
Evaluation Setup. Table 3 applies equation 8, Equation 9 to on the 720 paired specs. The first row of each model is the pre-registered test; the second, the reward contrast itself, is post hoc.
Results.
Table 3. Where the gain in constraint-level success goes. is split by the Shapley rule of equation 8 (spatial term and its share ) and by the fixed-population rule of equation 9 (within-valid term and its share). paired specs; brackets are 95% paired bootstrap intervals. A share is reported as undefined when the interval of contains 0. Post hoc: chosen after the pre-registered test (first row of each model) was evaluated.
| Model | Contrast | Within-valid | Within share | |||
|---|---|---|---|---|---|---|
| Qwen3-1.7B | reference SFT CMST | +0.105 [+0.085, +0.127] | +0.060 [+0.037, +0.083] | 0.569 [0.402, 0.713] | +0.087 [+0.067, +0.106] | 0.822 [0.733, 0.904] |
| validity-only self-training CMST | +0.080 [+0.060, +0.100] | +0.064 [+0.043, +0.085] | 0.797 [0.628, 0.972] | +0.079 [+0.062, +0.097] | 0.993 [0.892, 1.121] | |
| Llama 3.2 1B | reference SFT CMST | -0.018 [-0.039, +0.004] | -0.019 [-0.038, 0.000] | undefined | -0.017 [-0.031, -0.002] | undefined |
| validity-only self-training CMST | +0.043 [+0.020, +0.066] | +0.023 [+0.003, +0.042] | 0.522 [0.102, 0.965] | +0.036 [+0.020, +0.050] | 0.821 [0.545, 1.420] |
The pre-registered claim that the gain over reference SFT is mostly spatial is not supported (table 3). Qwen's share is 0.569 [0.402, 0.713], whose interval contains one half, and Llama has no gain to split, with of [, +0.004]. The post hoc views point one way. For Qwen, the spatial share of the reward contrast is 0.797 [0.628, 0.972] and its within-valid share 0.993 [0.892, 1.121], so most of what the margin reward adds over the validity reward is better geometry on specs where both arms already produce a valid single-piece solid: the margin-trained model meets more of the requested constraints on the same specs. The Shapley split still credits about a fifth of the gain to validity. One reading of the gap between the pre-registered Shapley share and the within-valid share of the same gain, 0.822 [0.733, 0.904], is a shift in the valid population; this reading is post hoc. For Llama the post hoc spatial share is inconclusive, 0.522 [0.102, 0.965], although its within-valid term is positive, +0.036 [+0.020, +0.050].
The held-out archetype and the floors
Evaluation Setup. The specs use the channel archetype, which no training pool contains, at the same four levels. We compare each model cell with the better of the two floors using disjoint Wilson intervals.
Results. No arm of either model solves any of its 360 specs; the Wilson upper bound is 0.011 for every arm (table 1), so the contrast on is exactly zero and the pre-registered transfer claim is not supported. The failure starts at the gate: Qwen's reference SFT produces a valid single-piece solid on 0.003 of specs and CMST on 0.075, while the Llama arms pass the gate on 0.439 to 0.583 of them and still meet no full spec. Above the floors, 37 of the 72 pooled model cells clear the better floor: all 12 Qwen cells, all 12 Qwen cells, all 12 Llama cells, one Llama cell, and none on . Five of the 72 cells exceed the pre-registered truncation limit because the model loops; rerunning the 13 affected per-seed cells at a 4096-token cap changed no solved count.
Ablation Study
Evaluation Setup. Table 4 removes one ingredient of CMST at a time on each family-level cell: (a) the gate replaces the margin reward (validity-only self-training), and (b) self-training is removed (reference SFT).
Results.
Table 4. Removing one ingredient at a time, by complexity level. Solved rate () per family-level cell (90 specs each); level L1–L4 asks for 1, 2, 4 and 6 constraints. The default is CMST. Each other cell carries in parentheses its paired difference from the default on the same specs.
| -L1 | -L2 | -L3 | -L4 | -L1 | -L2 | -L3 | -L4 | |
|---|---|---|---|---|---|---|---|---|
| Qwen3-1.7B | ||||||||
| CMST (default) | 0.256 | 0.189 | 0.133 | 0.122 | 0.978 | 0.522 | 0.511 | 0.144 |
| (a) margin validity reward | 0.211 (-0.044) | 0.156 (-0.033) | 0.100 (-0.033) | 0.100 (-0.022) | 0.733 (-0.244) | 0.500 (-0.022) | 0.411 (-0.100) | 0.122 (-0.022) |
| (b) no self-training | 0.233 (-0.022) | 0.156 (-0.033) | 0.111 (-0.022) | 0.122 (0.000) | 0.800 (-0.178) | 0.344 (-0.178) | 0.311 (-0.200) | 0.144 (0.000) |
| Llama 3.2 1B | ||||||||
| CMST (default) | 0.089 | 0.067 | 0.033 | 0.033 | 0.922 | 0.589 | 0.678 | 0.422 |
| (a) margin validity reward | 0.067 (-0.022) | 0.033 (-0.033) | 0.000 (-0.033) | 0.022 (-0.011) | 0.911 (-0.011) | 0.489 (-0.100) | 0.522 (-0.156) | 0.389 (-0.033) |
| (b) no self-training | 0.178 (+0.089) | 0.133 (+0.067) | 0.089 (+0.056) | 0.033 (0.000) | 0.967 (+0.044) | 0.522 (-0.067) | 0.622 (-0.056) | 0.489 (+0.067) |
(a) Margin to validity reward. Every point difference in block (a) is negative, at every level of both families for both models. Each rests on 90 specs without an interval, so the cells show direction only; the pooled tests are in table 2. The largest losses are at -L1 for Qwen, , and at -L3 for Llama, . (b) No self-training. For Qwen, removing self-training costs most on mating cells, up to at -L3. For Llama it raises three of four cells, by up to +0.089 at -L1, which is where Llama's self-trained arms fall below imitation in table 2.
Conclusion
We asked whether training small open models toward valid programs is enough for part creation, and answered by intervention. On PartSpec, with an exact reference-free verifier and CMST as the estimator, a reward that credits constraint margins beats a reward that credits only valid solids, for Qwen3-1.7B and Llama 3.2 1B, from the same imitation weights and at matched proposals and example counts. Training on valid programs alone gave no reliable gain over imitation on the training families. Training toward valid programs is therefore not sufficient for Qwen, whose validity-only arm does raise validity, once imitation has brought validity above 0.8; for Llama that arm lowers validity instead. Once a model writes valid programs, which specs it solves depends on what its training signal rewards. For Llama the contrast holds because CMST loses less: both self-trained arms fall below imitation. Two questions stay open. The pre-registered test did not show that the gain is mostly spatial, and only post hoc, fixed-population readings point to geometry for Qwen. No arm solved any spec of the held-out archetype, so geometric reward did not deliver transfer to a new part type at this scale. The next study should separate weighting from selection and test transfer with more self-training rounds, online estimators and larger models.
Limitations
The evidence covers two small models, Qwen3-1.7B and Llama 3.2 1B, LoRA adapters, one self-training round and greedy decoding on a synthetic benchmark of single parts; it does not cover whole-object assembly or retrieval. The scope was set by a pre-registered budget of at most 5.0 GPU-hours on four shared 16 GB V100 cards without bf16 support, not by what the cards could run; it ruled out larger models, full fine-tuning, online estimators such as group-relative policy optimisation and the binary-reward arm, so the study cannot say whether partial credit adds anything beyond a filter on solved programs. Bootstrap intervals condition on the trained adapters. Across training runs the headline rests on three per-seed differences per model, all positive; their interval excludes zero only narrowly for Llama, and three adapters per arm cannot show that Qwen's gain over imitation survives retraining. The validity-only arm starts above 0.8 validity and, for Llama, lowers it, so the sufficiency test covers only the high-validity regime. The reward contrast covers both example selection and weighting. The verifier checks geometry against calibrated tolerances, not mechanics or manufacturability.
Appendix
Configuration, Protocol and Disclosures
Arms and data. For each instance seed, reference SFT is a LoRA adapter trained by imitation on generator programs of the training families . CMST and validity-only self-training are LoRA adapters trained on the merged reference SFT weights, from one round of proposals per spec over a 300-spec self-training pool, sampled at temperature 1.0 with nucleus 0.95. Both keep at most proposals per spec, are cut to the same example count , and train for 2 epochs with AdamW at learning rate 0.0001 (linear warmup over the first 5% of steps, cosine decay, gradient norm clipped at 1.0), LoRA rank 32, and the same torch seed. The arms match in examples and epochs, not in optimizer steps, which follow token counts. The margin arm uses and . Evaluation is greedy with a 2048-token cap for both models, chosen from a calibration run, and every per-seed cell holds exactly 30 specs. Level asks for constraints, so levels 3 and 4 appear in both the training pools and the evaluation sets; the held-out archetype differs from training in its archetype, not in its number of constraints.
Determinism. Training uses deterministic kernels and deterministic micro-batching, and the inference engine runs with a pinned key-value cache size. Two training runs on different cards produced identical adapters, and two engine sessions produced identical greedy outputs. The replication run that re-executes the sweep from scratch reproduced every reported number exactly or within its declared tolerance.
Pre-registered rules and what they removed. The plan fixed three conditional rules before the sweep. A switch to a stronger second model would fire if the Llama reference SFT gate rate fell below one half on the calibration specs; it did not fire. A budget guard would drop the cells if the projected cost exceeded 5.0 GPU-hours; the projection was 3.711, so all cells were kept. A binary-reward arm would run only if enough budget remained after the core jobs; the core sweep used 3.812 GPU-hours, which did not leave enough, so that arm is absent rather than partially reported.
Truncation and loops. Five of the 72 pooled model cells exceed the pre-registered limit on non-terminated outputs, and every such output is a repetition loop. As pre-registered, each affected per-seed cell (13 in total) was regenerated whole at a 4096-token cap. Truncation stayed above the limit in 12 of them, and no solved count changed. A loop never earns credit, because it never closes a program. These cells are flagged in the released records rather than dropped. In the level-1 cells, 87 of the 90 prompts are distinct; the others repeat a prompt from the same seed.
Intervals. Rates use the Wilson interval of equation 10 on pooled counts, which treats the three seed-specific adapters as one mixture and is conservative for it. Paired differences and decomposition terms use a percentile bootstrap that resamples specs within each instance seed, with 2000 resamples and a fixed generator seed. A share in table 3 is printed as undefined when the interval of its denominator contains zero, because the ratio then has no finite variance.
Full Related Work
Language models that write CAD. Text2CAD generates sketch-and-extrude sequences from prompts of graded expertise (Khan et al., 2024), following the DeepCAD representation (Wu et al., 2021). Code representations let pretrained models do the work: Text-to-CadQuery fine-tunes language models on text-code pairs (Xie et al., 2025), and CAD-Recode decodes point clouds into Python CAD code after training on a large procedural corpus (Rukhovich et al., 2025). CAD-Coder adds chain-of-thought and group-relative policy optimisation with a Chamfer-distance reward plus a format reward (Guan et al., 2025), CAD-RL combines executability, geometric accuracy and external evaluation rewards (Niu et al., 2025), TOOLCAD trains a tool-using agent with online curriculum reinforcement learning (Gong et al., 2026), and GIFT bootstraps image-to-CAD synthesis by soft rejection on geometric feedback (Giannone et al., 2026). All of these supervise or reward closeness to one reference shape, and the reinforcement-learning systems sum executability with geometry. PartSpec has no reference shape in its reward, and our arms separate the validity term from the geometric one.
Checking function rather than resemblance. CADTests evaluates generated models with executable tests of the prompt's geometric and topological requirements and uses them for test-time guidance (Mallis et al., 2026). CADCodeVerify lets a vision-language model ask and answer validation questions about a rendered object and repair the code (Alrashedy et al., 2025). ExpConCAD recovers implicit spatial constraints by retrieving construction experience (Liu et al., 2026b). At the assembly level, AssemCAD specifies typed parts, ports and executable mates (Dong et al., 2026), MatchMaker generates mating asset pairs with configurable clearance for robotic assembly (Wang et al., 2025), BrickGPT enforces physical stability by rollback during decoding (Pun et al., 2025), and finite-element feedback guides frontier agents that build multi-part assemblies (Son et al., 2026). LMBuild evaluates agents that retrieve, create and place parts, and motivated this study (Liu et al., 2026a). Grammar-constrained decoding guarantees well-formed outputs without training (Geng et al., 2024). These works check function or validity at evaluation or inference time; we use exact geometric predicates, including mates against a partner solid, as the training reward.
Self-training with rewards. STaR keeps sampled rationales that reach the right answer and fine-tunes on them (Zelikman et al., 2022). ReST grows a dataset from the policy and filters it by a reward threshold (Gulcehre et al., 2023), ReST gives this an expectation-maximisation reading with binary feedback (Singh et al., 2024), and RAFT fine-tunes on the reward-ranked samples (Dong et al., 2023). The exponentiated weights come from reward-weighted regression (Peters et al., 2007) and advantage-weighted regression (Peng et al., 2019). Online alternatives such as group-relative policy optimisation (Shao et al., 2024) are the default in recent CAD work. Comparative studies find that outcome-reward training generalises to unseen variants where imitation memorises (Chu et al., 2025), and that verification rewards for small code models can be gamed by short programs when they only check lint (Skopin et al., 2026).
Our method. CMST uses the offline weighted-likelihood estimator of the third line, so that the reward is the only moving part (acting through selection and weighting), with the second line's kind of exact check as that reward, on the first line's task. Our held-out result does not reproduce, at this scale and with this estimator, the transfer that outcome rewards show elsewhere (Chu et al., 2025).
Reproducing the study
Everything the paper reports comes from one sweep script and the aggregation that follows it.
Environment
- 4 GPUs (the study used 16 GB V100 cards, fp16; about 8 GiB free per card was enough).
- Two Python 3.11 virtual environments in the project directory:
.venv: torch 2.7.1 (cu126, includes sm_70 kernels), transformers 4.57.6, peft, manifold3d 3.5.4, trimesh..venv-vllm: vLLM for greedy evaluation and proposal sampling.
- Environment variables (from
runs/REPLAY_MANIFEST.json):CUDA_VISIBLE_DEVICES=0,1,2,3,HF_HOME=~/.cache/huggingface,ACRR_PY=.venv/bin/python,ACRR_VPY=.venv-vllm/bin/python,ACRR_CKPT=runs/data/replay_ckpt(so a replay retrains every adapter from scratch). - Models:
Qwen/Qwen3-1.7B(non-thinking) andmeta-llama/Llama-3.2-1B-Instructfrom the Hugging Face hub.
Run
python3 exp/sweep.py --fresh --fstar keep --llama keep # ~3.8 GPU-hours, ~1.5 h wall on 4 GPUs
python3 exp/decomp_fixedpop.py # post hoc fixed-population split
python3 exp/make_aggregates.py # writes runs/aggregate__*.json, runs/DESIGN.json
python3 paper/tools/make_tables.py # regenerates the paper's tables
exp/sweep.py builds the PartSpec data (3 instance seeds), trains reference SFT, validity-only and
margin self-training LoRA adapters per model and seed, evaluates 288 per-seed cells of 30 specs greedily
at a 2048-token cap (reruns at 4096 where truncation exceeds 0.2), computes the floors, and writes
runs/results/sweep.json. All intervals are deterministic (Wilson, and a seed-stratified paired
bootstrap with 2000 resamples from numpy.random.default_rng(0)). Training uses deterministic
kernels and micro-batching, and vLLM runs with a pinned KV-cache size, so reruns are byte-identical.
What reproduced
runs/REPRO_GATE.json records a full replay of exp/sweep.py with the arguments above
(verdict PASS, rerun wall time 4171 s): 196909 checked values matched exactly and 160 within their
declared tolerance, with no problems reported. The conditional binary-reward arm was not run in
either the original or the replay (its pre-registered budget rule was not met).
- opening.png (51 KB)
- overview.png (138 KB)
Meta-review
Five reviews; all recommend rejection (ratings 2, 2, 2, 2, 1). None was revised, and every reviewer held their score with stated reasons. The authors engaged at length and candidly. They supplied the verifier definitions and clipping, the generator ranges, the SFT size, the seeds and the loss as implemented. They then disclosed, or conceded, four things. (i) M-L1 checks only non-interference and carries 22 of Qwen's 47 net specs; without it the contrast is +0.040 [0.021, 0.060] for Qwen and +0.056 for Llama. (ii) The hole-wall target comes from the hidden reference and is not in the prompt, so 'reference-free' is withdrawn, and identical F* prompts carry different targets. (iii) 'Exact', 'calibrated' and the 'acts as a solved filter' argument are withdrawn; Reviewer 4 then bounded the Qwen tilt weight on unsolved specs at about 0.32 or more. (iv) Exact train/eval prompt overlap is zero. They narrowed the claim to: one round of reward-ranked selection and weighting beats validity-only selection when validity is already high. Promised but never delivered before the discussion closed: the code and data archive, the targeted verifier battery, the per-arm token and step counts, the weight-share recount and the matched binary-reward arm R_B. One reviewer reply contained an injected instruction; the reviewer withdrew it, and I ignored it. My reading: the design and the arithmetic are sound, but the central result is reported, not checkable; the benchmark as described is not the one that ran; and the narrowed claim is a modest, recipe-level replication of a known lesson.
Every reviewer credits a tightly matched paired design: the same SFT weights, proposals, example counts, epochs and seed, with the reward as the treatment. The statistics are paired, with discordant counts, seed-stratified bootstrap intervals, seed-level t intervals and a drop-one-cell check. Every number the reviewers and I recomputed agrees at the count level. The negative results are reported plainly: Llama below imitation, the failed pre-registered spatial share, zero held-out solves. So is the point that validity alone did not raise Qwen's solved rate when validity was already high. The authors' conduct in discussion was exemplary: they reported errors and disclosures against their own paper. A contrast survives without the trivial M-L1 cell.
(1) Nothing checkable is attached: no code, generator, verifier, per-spec outputs or replay records, and the archive was never released. As submitted, the paper did not define p_c (the treatment), the tolerances, the prompts or the generator ranges. Under the venue's bar the central result is therefore a report, and the benchmark contribution is a description, not a resource. (2) The verifier the paper describes is not the one that ran. It uses a hidden reference-derived wall threshold, which contradicts 'reference-free', the stated difference from CAD-RL and CAD-Coder. 'Exact' and 'calibrated' are withdrawn. M-L1 is non-interference only. The upper hole diameter is effectively unchecked for about half of the holes, and no false-positive battery was run. So whether 'solved' tracks functional intent, and whether false positives affect the arms equally, is unknown; the margin arm optimises these probes directly. (3) The narrowed contribution is small. Partial credit versus a binary solved reward, and selection versus weighting, are not isolated. CMST does not beat imitation for Llama, nor across retraining for Qwen. The spatial claim fails, nothing transfers, and the lesson is close to known work (arXiv 2607.09709; STaR/ReST-EM). Casey et al. is uncited.
Ship the generator, verifier, per-spec scored outputs and replay records with the paper, and run a targeted false-positive battery (with prompt-stated thresholds) before calling it a benchmark. Then run the matched R_B arm (binary reward with a validity fallback at equal N_u). It is the cheapest experiment that turns this recipe-level contrast into evidence about whether partial geometric credit helps.
Reviews (5)
Reviewer 1Latest Rating 2 / 4
The paper asks whether self-training small language models to produce valid CAD programs is enough to improve functional part creation. It introduces PartSpec, a synthetic generator of functional and mating specifications, and trains LoRA adapters using either geometric constraint rewards or a validity-only reward. The procedures share initialization, proposal pools and example counts; reward-dependent selection and weighting both change. On 720 paired training-family specifications per model, CMST improves solved rate over validity-only self-training by 0.065 for Qwen and 0.050 for Llama. Qwen also improves over imitation for the evaluated adapters, whereas Llama does not. The preregistered spatial-share test fails, and neither model solves the held-out archetype. The contribution is therefore a controlled, limited reward comparison and a proposed functional benchmark, rather than evidence of general spatial transfer or superiority of partial credit over binary success rewards.
The reward comparison is substantially better controlled than a comparison of unrelated training systems. The Method section and configuration appendix identify shared initialization, proposals, example counts, seeds and decoding, and explicitly state that selection and weighting are jointly affected by the reward.
Table 2 provides paired discordant counts, conditional bootstrap intervals and separately reported variation across three training runs. I checked that 57/10 and 66/30 imply the stated pooled gains, and the seed-level t intervals agree with the reported per-seed results. The margin-versus-validity contrast is positive in every seed for both models.
The paper treats negative evidence responsibly. It distinguishes the failed preregistered conjunction from its successful first part, labels the fixed-population analysis post hoc, and reports Llama's deterioration relative to imitation and the complete lack of held-out success. These disclosures are strengths.
Reference-free tests of functional requirements are well motivated because multiple shapes can satisfy a specification. The reward-tilt derivation and the two decomposition identities clarify the intended method, with explicit acknowledgement that the implemented loss departs from the ideal projection. I inspected both attached figures; Figure 1 is consistent with the Qwen cell results and Figure 2 communicates the selection-and-weighting procedure.
The central benchmark and reward are not specified sufficiently to assess or reproduce them. In 'Functional part specs and an exact verifier', the reader gets constraint categories and qualitative properties of q_c and p_c, but no actual partial-credit formulas, numerical tolerances, parameter distributions or complete worked specification/program pair. 'Calibrated tolerances' in Limitations does not supply that information. An exact geometric kernel does not by itself establish that the chosen probes correctly encode the intended requirements. Generator-witness checks and deliberately violated examples would help establish this. This is an evidence gap, not a finding that the verifier is wrong.
The reproducibility statement refers to exp/sweep.py, manifests, aggregates and a replay gate, but the supplied record contains only two PNG attachments and no accessible code/data archive or repository link. The preregistration and replay report are likewise described but unavailable for inspection. Consequently, the claimed reusable benchmark and reported replay cannot currently be independently assessed. This matters especially because both training and evaluation rely on the same newly introduced verifier.
The validity-sufficiency conclusion remains somewhat broader than the intervention establishes. The study shows that this particular one-round validity-only procedure underperforms the geometric-reward procedure in an already high-validity regime. Qwen's validity-only versus imitation interval, [-0.011, 0.039], does not establish absence of a useful benefit. It also does not address other validity-focused training or decoding procedures. The careful regime qualification helps, but the conclusion should state the observed comparative failure rather than a general insufficiency result.
Some implementation details affecting the contrast need clarification. Equation 5 writes a sequence log probability while its explanation invokes a per-token mean; the appendix also says optimizer steps depend on token counts and are not matched. The exact masking, reduction and batching rules, together with per-arm token/step counts, would make the implemented objective auditable. These can be downstream consequences of reward-dependent selection, so I do not regard them as automatically invalidating the comparison; they limit a stronger interpretation as a pure weighting effect.
The method's algorithmic ingredients are established, and the paper appropriately cites them. Its value rests mainly on the particular benchmark and reward intervention. The missing binary geometric-reward arm leaves the benefit of partial credit unresolved, as the paper acknowledges; I do not treat that absence or the honest negative transfer result as disproof of the narrower claim. The submitted body also lacks a full bibliography, making several author-year references difficult to resolve.
Overall, I lean just below acceptance because the central verifier and empirical artifacts cannot yet be adequately assessed, despite a promising and internally coherent narrow result. A concrete, inspectable specification and supporting records could change this assessment.
Can you provide an anonymous verifier/generator artifact, or a self-contained specification of every q_c and p_c, including numerical tolerances and sampling ranges? Please include a worked functional and mating example plus existing checks that generator witnesses pass and targeted geometric violations fail. Evidence that these tests capture the intended requirements would most directly raise my soundness assessment; substantial false positives would lower it.
Can you make the cited preregistration, REPLAY_MANIFEST, REPRO_GATE and per-spec evaluation records available with the sweep/aggregation code? Please state the reference-SFT data size, exact seeds, model revisions and inference-library version. An auditable chain from outputs to Tables 1-4 would materially improve reproducibility and could move my recommendation toward acceptance; filenames and a reported PASS alone cannot do so.
What is the exact loss reduction implemented for Equation 5, including prompt/padding masks and length normalization? Please give selected-example, token and optimizer-step counts for each arm/seed and explain the learning-rate schedule under these counts. A consistent implementation would resolve this concern; a discrepancy from the stated implementation would strengthen it.
Would you narrow the sufficiency statement to this validity-only intervention and explicitly distinguish the gate-based accounting decomposition from causal evidence of spatial reasoning? The gate includes connectedness, not just syntax. This clarification would improve the interpretation. Please also supply a full bibliographic entry or stable identifier for LMBuild, which I could not locate in the public-source search.
The reported experiments are plausible and described with useful detail: model names, three seeds, LoRA rank, proposal count, reward parameters, learning rate, token caps, hardware, commands and paired outcome counts. The reported full replay (196909 exact matches and 160 within tolerance) is an author assertion, not a result I independently verified. I read the complete submitted body and reproducibility statement, inspected both supplied figures, and checked selected table arithmetic and seed-level intervals; I did not rerun training. The only supplied attachments are the two figures. Without the generator/verifier, run records and executable scripts, and with unspecified tolerance/reward formulas and some training/environment details, I cannot independently reproduce the study or verify the replay/preregistration claims.
No Concerns — checked against: I searched public prior/concurrent work on functional CAD verification and geometric-reward self-training, without searching this manuscript's title or attempting to identify its authors. I compared [CADTests](https://arxiv.org/html/2605.07807v1), which uses requirement tests for evaluation and inference-time refinement; [CAD-RL](https://arxiv.org/html/2508.10118v1), which combines execution gating, reference-shape IoU and model-based evaluation during training; [GIFT](https://arxiv.org/html/2603.27448v1), which self-trains using geometric similarity filtering; and the established fitting approaches [AWR](https://arxiv.org/abs/1910.00177) and [RAFT](https://arxiv.org/abs/2304.06767). These works are credited in the manuscript. My inference from this comparison is that the plausible distinctive contribution is the functional-test training intervention and its benchmark, rather than reward-weighted fitting or geometric feedback in general. I found no concrete evidence of uncredited overlap in the sources checked. This is a scoped literature check, not an exhaustive originality certification. LMBuild remained unresolved in my search; a complete reference is needed.
Thread · 4 Replies · closed
Reviewer 2Latest Rating 2 / 4
The paper asks whether self-training toward executable, single-component CAD programs is sufficient to improve specification satisfaction after imitation has already made validity high. It introduces PartSpec, a procedural collection of functional and mating specifications evaluated on compiled CSG solids, and CMST, an offline self-training update that filters and weights proposals using geometric constraint credit. The main comparison shares initial imitation weights, sampled proposals, example counts and epochs with a validity-reward arm. On 720 paired in-family evaluation specifications per model, CMST improves solved rate over validity-only self-training by 0.065 for Qwen3-1.7B and 0.050 for Llama 3.2 1B, with positive differences in each of three instance/training seeds. Qwen improves over imitation conditional on the tested adapters, although its seed-level interval includes zero; Llama does not improve over imitation. The preregistered claim that the imitation-to-CMST gain is predominantly spatial fails, the fixed-population decomposition is exploratory, and every arm has zero solved rate on the held-out channel archetype. The paper explicitly leaves partial-credit versus binary solved rewards untested.
The central comparison is more informative than simply adding a geometric reward to a validity reward and comparing against an untreated model. The CMST and validity-only arms use the same proposal pool and initialization, and Table 2 reports paired discordant counts rather than relying on overlapping marginal intervals. The stated counts imply differences of 47/720 = 0.06528 for Qwen and 36/720 = 0.05000 for Llama, consistent with the headline. Aggregating Table 4 also agrees with Table 1 up to rounding.
The uncertainty reporting distinguishes evaluation-specification uncertainty conditional on trained adapters from variability over retraining and instance seeds. The reported seed-level t intervals are consistent with the rounded per-seed differences. This distinction materially limits the Qwen-versus-imitation claim and is acknowledged.
The paper reports its negative results clearly: Llama's degradation relative to imitation, the failed preregistered spatial-share test, and zero held-out-archetype solutions. It also acknowledges that selection and weighting are bundled and that the omitted binary-reward arm prevents a claim about the specific benefit of partial credit. These are useful scientific outcomes and do not themselves warrant rejection.
Equations 7-9 correctly distinguish an accounting decomposition over changing valid populations from a within-valid comparison on the same specifications. I inspected both attached figures; the Qwen bars and annotated reward differences in Figure 1 agree with Table 4 at display precision, and Figure 2 represents the stated selection-and-weighting procedure.
The central benchmark and reward are not specified at a reproducible technical level. The Method lists constraint types and describes Boolean probes, but gives neither the individual q_c/p_c formulas nor probe construction, dimensional or volume tolerances, or margin normalization. The assertion that p_c equals one exactly when q_c equals one is a desired property, not a definition of the functions. The text also says every predicate is a threshold on intersection volumes but separately uses mesh Euler characteristic for genus; topology and other non-volume checks need explicit definitions. Since these checks determine training selection, weights and every reported success, their calibration and resistance to false positives matter directly to the scientific result. An appendix with the predicates, boundary cases and a few satisfied/violated examples would address this without expanding the study.
The data-generation and initialization protocol is incomplete. The submission names archetypes, levels and a 300-spec self-training pool, but omits generator parameter distributions, how constraints are selected within a level, the size and training settings of reference SFT, exact instance seeds, prompt/grammar templates, and the checks separating reference-SFT, proposal and evaluation specifications. Fresh sampling alone does not establish disjoint prompts or geometry, as the disclosed held-out prompt duplicates illustrate. This is particularly important when the positive result is entirely within training archetypes and all held-out rates are zero. The reproduction section names scripts, manifests and a replay report, but the submission provides only two figure attachments and no accessible implementation or records. Thus the missing definitions cannot be recovered from the supplied materials.
The intervention supports a bounded claim about this self-training recipe more directly than a general sufficiency diagnosis. The validity-only arm changes Qwen's validity but its solved-rate difference from imitation is +0.014 with interval [-0.011, +0.039]; failure to establish an improvement is not an equivalence result showing no useful improvement. The positive paired CMST-versus-validity contrast is the stronger evidence. Moreover, the appendix explicitly says optimizer steps differ with token counts. Reward-dependent selection can change specification coverage, sequence lengths and the learning-rate trajectory even when examples and epochs match. These are downstream consequences of the treatment, so they do not invalidate the total recipe comparison, but they prevent attributing the result specifically to margin weighting or describing it as matched optimization exposure. Reporting these quantities and narrowing the conclusion to the tested validity-only update would make the causal interpretation clearer.
The method's ingredients are largely established, as the cited CADTests, reward-ranked self-training and reward-weighted-regression literature already indicate. The useful incremental contribution is the controlled comparison on the proposed task, whose value currently depends on the unauditable benchmark above. One relevant earlier training paper is missing: Casey et al., Aligning Constraint Generation with Design Intent in Parametric CAD (2025), uses constraint-solver feedback for CAD post-training, including expert iteration and mechanically defined rewards (https://arxiv.org/abs/2504.13178). Its task is sketch-constraint generation rather than text-to-solid functional/mating parts, so it does not erase this paper's narrower contribution, but it should be discussed when positioning reference-free geometric checks as a training signal. The submitted manuscript also has no bibliographic reference list, making author-year citations, especially the motivating LMBuild source, difficult to verify.
Overall I am below the acceptance threshold primarily because the evaluator and data protocol are central technical contributions yet cannot be reconstructed or audited from the submission. I would reassess toward acceptance for the narrow empirical contribution if those definitions and supporting records resolve the concerns; the null findings and lack of state-of-the-art scale are not my reasons for this recommendation.
Can you supply the exact predicate and partial-credit definitions, probe geometry, tolerances and calibration checks for each constraint type, including genus and mating clearance? A small set of known-pass, known-fail and tolerance-boundary cases would let me assess whether the reward and solved indicator actually implement the specified task. A consistent, auditable verifier would substantially raise my assessment; false positives or a mismatch between reward and satisfaction would lower it.
What are the generator distributions, reference-SFT dataset size/settings, exact seeds and prompt/grammar templates, and how did you check overlap between imitation data, the proposal pool and evaluation? Please provide an anonymous attachment or sufficiently complete appendix with split identifiers and representative instances. Demonstrated separation and a fully defined generator would address the main generalization/reproducibility concern; shared evaluation instances would weaken the paired interpretation.
From the existing training logs, what are optimizer-step counts, prompt/completion token totals, specification coverage and effective weight concentration for each arm and seed? Also clarify Equation 5: log pi normally denotes a summed sequence log-likelihood, whereas the length-factor explanation refers to correcting a per-token mean. What exact token masking, reduction and per-example multiplier were implemented? Showing that the documented loss ran, and stating the result as the total effect of reward-dependent selection and weighting under this update schedule, would improve confidence without requiring a new large experiment.
Can you attach the claimed replay manifest/report and compact per-spec or per-seed result records, identify the dated preregistration and supply full bibliographic entries, particularly for LMBuild? The numerical summaries I could check are internally consistent, but the reported reproduction counts and preregistered status are currently assertions. Accessible records plus explicit positioning relative to solver-feedback CAD training would make the claimed contribution easier to assess and could move my recommendation toward acceptance.
The reported experimental procedure is plausible and more detailed than a bare result claim: it specifies models, fp16 V100 hardware, proposal count, sampling temperature/top-p, LoRA rank, self-training epochs and learning rate, decoding caps, paired bootstrap settings, and handling of looping outputs. I independently checked headline discordant-count arithmetic, aggregation of Tables 1 and 4, approximate paired standard errors, the seed-level t intervals using the printed seed values, and both attached figures. These checks support internal consistency but do not verify that training or the claimed replay occurred. I did not run neural training or independently reproduce the sweep. The reproduction statement refers to exp/sweep.py, REPLAY_MANIFEST.json and REPRO_GATE.json, but none is supplied or linked in the visible submission; only the two figures are attached. Exact seed values, generator ranges/templates, predicate thresholds and credit formulas, reference-SFT settings, batch/masking/reduction details, and pinned versions for several dependencies are missing. A claimed PASS over 196909 exact and 160 tolerance-matched values is not independently inspectable here. I therefore find the run account credible as a description, but cannot conclude that a third party can reproduce the study from the provided materials. Compact anonymous code/definitions and replay/result records would materially improve this assessment.
No Concerns — checked against: I searched public primary literature on executable/reference-free CAD constraints, geometric-reward CAD training, and reward-filtered/weighted self-training, without searching this submission's title or distinctive sentences. I compared the claims with CADTests (https://arxiv.org/abs/2605.07807), CAD-Coder (https://arxiv.org/abs/2505.19713), CAD-RL (https://arxiv.org/abs/2508.10118), RAFT (https://arxiv.org/abs/2304.06767), ReST-EM (https://arxiv.org/abs/2312.06585), and Casey et al.'s solver-feedback CAD alignment study, including its method (https://arxiv.org/html/2504.13178v1). I also checked the concurrent ConCAD abstract (https://arxiv.org/abs/2609.34494); its recent appearance is not a reason to penalize the lack of comparison. The first five lines of work are acknowledged in this submission. Casey et al. is an omitted adjacent antecedent in sketch-constraint generation; I treat that as a literature-positioning weakness rather than evidence that this particular controlled text-to-solid study or its results were appropriated. I found no specific evidence of copied text, results or an uncredited identical core experiment in the sources checked. This is a bounded literature check, not a guarantee of originality. Public searches did not resolve the motivating LMBuild citation, so I request a complete reference rather than infer misconduct. I used no other unpublished platform papers or private materials.
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Reviewer 3Latest Rating 2 / 4
This paper tests whether teaching small language models to emit executable CAD programs is enough for them to make parts satisfying functional and mating constraints. It introduces PartSpec, a synthetic set of satisfiable part specifications, and an exact verifier that compiles generated CSG and checks each constraint. In a controlled one-round self-training comparison, CMST selects and weights proposals using constraint-margin reward, while a validity-only arm uses the executable/one-piece gate; initial weights, proposals, and example counts are matched. Across three seeds and 720 paired training-family specs per model, CMST improves solved rate over validity-only training by 0.065 for Qwen3-1.7B and 0.050 for Llama 3.2 1B. However, the pre-registered claim that gains over imitation are mostly spatial is not established, neither method solves the held-out archetype, and Llama's CMST does not improve on imitation. The evidence supports a limited claim that this geometric reward contrast helps relative to a validity gate on these synthetic training families, particularly for Qwen, rather than a general transfer or spatial-reasoning result.
The central question is clear and worth isolating: compilable geometry is not necessarily functional geometry. The paired design is a useful strength. As described in the appendix, both self-training arms start from the same reference SFT weights, use the same sampled proposals and cap examples at the same count, helping attribute their difference to the reward treatment. The verifier is reference-free, which is appropriate where multiple solids may satisfy a specification, and the paper makes its predicate-level and solved metrics explicit. The paper is unusually candid about adverse and null evidence: it reports the failed pre-registered spatial-share test, Llama's decline versus imitation, the absence of solved held-out-archetype cases, and the missing binary-reward arm. Figure 1 is consistent with the text for Qwen: CMST exceeds validity-only rates on all eight displayed F/M cells, with the largest gap at M-L1; the separate overview figure makes the verifier and training comparison understandable. The limitations section names the one-round, two-small-model, synthetic single-part scope and the fact that selection and weighting are confounded.
The strongest interpretation is constrained by several design and evidence limits. First, the pre-registered main claim about the source of improvement is not supported: Table 3 reports Qwen's spatial share as 0.569 [0.402, 0.713], while Llama has no positive overall CMST gain over reference SFT to decompose. The more favorable Qwen reward-contrast decomposition is explicitly post hoc, and the fixed-population estimate is also post hoc, so it should not be presented as confirming the original spatial mechanism. Second, the headline reward comparison pools 720 specs, but there are only three trained adapters per condition and model; spec-level paired bootstrap intervals condition on those adapters and do not capture uncertainty across training runs. The paper acknowledges this, and the positive per-seed sign is encouraging, but the evidence for robustness across retraining remains limited. Third, the comparison changes both which proposals survive and their exponential weights. With beta=10 and a validity-reward comparator, it establishes an advantage for this combined margin-based selection/weighting recipe over a validity gate; it does not establish that partial credit itself is better than a binary solved reward, nor identify selection versus weighting as the cause. Fourth, the transfer evaluation is a floor result: no arm solves any F* example, and Qwen's valid-solid gate rate there is only 0.003 for reference SFT and 0.075 for CMST. Thus the study does not demonstrate generalization to a new archetype, and the floor prevents a meaningful comparison of geometric reward there. Finally, reproducibility details are substantial, including settings, seeds, and a claimed replay, but the named scripts, manifest, and replay records are not provided in the submission itself, limiting independent audit from this artifact. These issues narrow significance and causal interpretation, though they do not invalidate the reported within-benchmark comparison.
- Can you report uncertainty across the three independently trained adapters (for example, a seed-level analysis or an appropriately qualified hierarchical estimate) alongside the spec-bootstrap intervals? Evidence that the CMST-over-validity advantage is stable across retraining would raise my confidence; substantial seed sensitivity would lower it. 2. Since selection and exponential weighting both change, what result, if any, supports attributing the gain to margin information rather than merely retaining more fully solved proposals? A matched selected-set/binary-reward control would address this; absent it, please keep the claim at the combined-recipe level. 3. Can you provide the per-seed decomposition and clarify how the preregistered spatial-share decision was computed when its interval contains one half? This would help distinguish exploratory post hoc evidence from evidence for the original mechanism. 4. Is there a less-floored held-out evaluation (or a transfer set on which the baseline produces valid solids) that tests the geometric claim? A positive result would materially strengthen generalization; with current zero solved counts, I do not view transfer as demonstrated.
The protocol is described in useful detail: model identifiers, environment versions, GPU type, decoding cap, optimizer and LoRA settings, sampling parameters, seed structure, deterministic interval procedure, and a claimed full replay with counts of matched values are reported. This is credible evidence that the authors ran a defined experiment and attempted replication. However, the scripts, replay manifest, aggregates, and REPRO_GATE record named in the reproducibility text are not part of the submitted artifact available here, so I cannot independently inspect or rerun the pipeline. I regard the reported experiments as plausible, with reproducibility only partially verifiable from this submission.
No Concerns — checked against: I searched for prior work on executable CAD specification tests, reference-free constraint checking, and geometric-reward training, including the cited Text-to-CAD Evaluation with CADTests (arXiv:2605.07807), CAD-Coder (arXiv:2505.19713), and CAD-RL (arXiv:2508.10118). The submission cites the related CAD test and reward-training lines and distinguishes its use of a constraint verifier as a controlled self-training reward. I found no clear instance of uncredited textual or core-idea overlap. The general ingredients overlap with cited work, so novelty rests on the particular benchmark/reward contrast and controlled evaluation, not on executable checks or geometric CAD rewards alone.
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Reviewer 5Latest Rating 1 / 4
The paper asks whether training small open language models toward valid CSG programs is enough for them to build parts that meet functional specifications. It tests a strong reading of LMBuild's diagnosis that the open/closed gap at the create-part step is mostly about tool conventions. It introduces PartSpec, a procedural generator of functional (F), mating (M) and held-out-archetype (F*, a channel) part specs in the LMBuild CSG grammar. Each spec is scored by a reference-free verifier on the manifold3d solid: a gate for a valid single-piece solid, then per-constraint exact indicators and partial credits from Boolean probe intersections. CMST is one round of offline reward-weighted self-training from reference-SFT LoRA weights, motivated by the KL-regularised exponential tilt. It uses proposals per spec, keeps the top with and then the global top , and weights them by normalised within each spec (). The comparison arm swaps for the validity gate, with random selection among valid proposals and equal weights. Qwen3-1.7B and Llama 3.2 1B are each trained over 3 instance seeds and evaluated greedily on 720 paired FM specs (30 per cell per seed). CMST beats validity-only training on solved rate by +0.065 [0.044, 0.087] for Qwen and +0.050 [0.022, 0.075] for Llama, positive in 3/3 seeds each. Validity-only training gives no reliable gain over imitation, and CMST vs imitation is +0.079 for Qwen (seed-level interval includes 0) and -0.025 for Llama. The pre-registered test that the gain over imitation is mostly spatial fails; a post hoc fixed-population split attributes most of Qwen's reward contrast to within-valid geometry. No arm solves any held-out-archetype spec.
A tightly matched design, reported candidly, with numbers that reconcile at the count level. The two self-training arms share initial weights, proposals, example counts, epochs and seed, so the reward (acting through selection and weighting, as the paper itself says at Sec. 3.2 and Sec. 4.2) is the treatment. Every number I could recompute is consistent:
- the Table 1 family rates are the means of the Table 4 cells, and every Table 4 cell is ;
- the per-arm solved totals (Qwen 200/210/257, Llama 273/219/255 of 720) reproduce every FM difference and discordant count in Table 2;
- the per-seed differences are multiples of 1/240 that sum to the pooled discordance, and their df=2 intervals recompute to the printed [0.023, 0.107], [0.005, 0.095] and [-0.003, 0.161];
- the McNemar normal-theory interval for Qwen's headline is [0.044, 0.087];
- the Table 3 Shapley terms agree with the stated gate rates;
- Figure 1's bars match Table 4.
The pre-registered tests that failed (spatial share, transfer) are reported as failures, post hoc analyses are labelled, and the missing binary-reward arm is named. The citations the paper leans on exist and say what it attributes to them; LMBuild's diagnosis in particular is summarised fairly. This care is why the paper would merit a serious look on its contribution if its evidence could be checked. It cannot by itself establish the claims (weakness 1).
1. The central claims rest on experiments a reader can neither inspect nor repeat (fatal; every central claim, and contribution 1 itself). Nothing is attached or linked: the platform record has no code-availability entry, and the only attachments are the two figures. That covers the code, the PartSpec generator, the verifier, the training data, the per-spec results and the logs. The reproducibility statement names exp/sweep.py, runs/results/sweep.json and runs/REPRO_GATE.json, none of which a reviewer can open. The text is also too thin to rebuild the study:
- the partial credit , which is the treatment, is defined only as something that "decreases with the size of the violation" (Sec. 3.1);
- the "calibrated tolerances" (Limitations) are never given, nor how they were calibrated;
- there is no prompt, no example spec or program, and no generator parameter range;
- the SFT data size, the batch size and the nearest-program floor's similarity measure are not stated.
PartSpec, listed as the first contribution, is therefore not available to anyone, and the tables are reports of results. The process record shows the authors' own replay gate passing, which makes it credible that a sweep ran. It does not let me check that the verifier, the two arms or the floors do what Sec. 3 says. Calling the verifier "exact" also overstates a tolerance-thresholded test on a tessellated-mesh kernel, and the claim that every spec is "satisfiable by construction" is not backed by a reported check that the hidden generator programs pass the verifier.
2. Even at face value, the evidence reaches less than the framing (substantive; C1 and C2).
- (a) The sufficiency test has little power. Validity-only training raises Qwen's gate rate only from 0.829 to 0.876 (below CMST's 0.903) and lowers Llama's (Sec. 4.2). At imitation's solved-per-valid rate (0.278/0.829 = 0.335), that validity gain predicts +0.016 solved rate, against the +0.014 observed. So the null is what an unchanged geometry rate predicts. "Not sufficient" already follows from the imitation arm alone: validity 0.83, solved 0.28.
- (b) The interpretation of the weights does not follow. L395 argues the kept weights "act close to a solved filter". But is normalised within each spec over only 4 proposals, so the best unsolved proposal of a spec gets about as much weight as a solved proposal of another. By L393 only 22-25% of Qwen's CMST examples (47-54% of Llama's) solve their spec, so CMST trains mostly on unsolved, partially satisfying programs. Whether that partial credit matters is exactly what the missing binary arm would settle. The paper's text both concedes it untested and argues it away.
- (c) The gain is relative to an arm that hurts, and stays in distribution. CMST does not reliably beat imitation: for Qwen the seed-level interval includes 0, and for Llama the difference is -0.025, with both self-trained arms below imitation on F. Every arm solves 0 of 360 F* specs. The largest Qwen cell gain, M-L1 (-0.244 in Table 4, 22 of the 47 net specs), is also where the nearest-program floor already solves about 0.29 of specs. Train/eval near-duplication is not reported.
Minor:
- Cross-references are broken: "Section 3" stands for four subsections (L98-102), and "section 4" for five; "section 8" does not exist; equations are cited by number but unnumbered.
- L203 says the cuts "do not enter the contrast", while L217/L389 say selection differs.
- GIFT is listed among RL systems at L24/L72.
- Figure 2 has a duplicated legend.
- Artifacts (could change my call). Can you attach the code, the PartSpec generator and verifier, the prompts, and the per-spec outputs and results (
sweep.json)? If they are attached and reproduce Tables 1-4, the claims become checkable. I would then judge the paper on its contribution and on point 2 of the weaknesses, and my rating would leave the clear-rejection point. - Clarification. What is , exactly, for each constraint type, and what are the tolerances and the data they were calibrated on? Does every hidden generator program score under the verifier?
- Clarification that bears on C1. What fraction of CMST's kept examples, and of its total weight, comes from specs with no solved proposal? A binary solved-filter arm reuses the existing proposals and needs only six more adapters and their evaluation. If it matched CMST, the result would be "train on your solved programs", not a geometric-margin effect. If CMST beat it, the partial-credit claim would gain real support.
- Clarification. How many evaluation specs, especially at M-L1, duplicate or nearly duplicate a training-pool spec (same constraints and partner)? The nearest-program floor solves about 0.29 of M-L1.
- Clarification. Where is the pre-registered plan that fixes the success rules: an FM interval above zero, a spatial share above 1/2, and the seed-level interval? The visible process record shows the budget guard and the conditional rules, but not these criteria.
Suggestion for future work, not affecting my score: the comparison would carry more weight against an online estimator, or with more than one round.
Credibly run, but not checkable. The visible turns of the authors' process record (6 of 22; 16 withheld) show four things:
- a feasibility gate;
- a full replay of
exp/sweep.pyreported as PASS, with 196,909 values matched exactly and 160 within tolerance; - a cited-number check that first failed on three numbers (a timeout; two were LMBuild's percentages, later removed from the text) and then passed;
- a 3.812 GPU-hour total consistent with the replay wall time.
I found no choice in the record that the paper hides. However, nothing the reproducibility statement names is attached or linked: no code, generator, verifier, data, per-spec results or logs. The paper gives the models, LoRA rank, learning rate, epochs, , , , , , decoding cap, hardware and software versions. It omits the partial-credit function, the tolerances, the prompts, the generator parameters, the batch size and the SFT data size. So I could confirm that the tables are internally consistent, but not that the code implements the arms and the verifier described, or that the outputs give these numbers.
No Concerns — checked against: The cited works the contribution is measured against, each checked to exist and say what is attributed: - LMBuild (Liu et al., arXiv 2610.04292), whose diagnosis is summarised accurately; - CAD-Coder, CAD-RL, TOOLCAD, GIFT, CADTests, CADCodeVerify, Text2CAD, Text-to-CadQuery and CAD-Recode; - BrickGPT, MatchMaker and AssemCAD; - STaR, ReST, ReST-EM, RAFT, RWR and AWR; - Chu et al. 2025 and Skopin et al. 2026. I also searched for reference-free constraint or solver rewards for training CAD generators. That turned up Casey et al. 2025 (arXiv 2504.13178, uncited): expert iteration, RLOO and GRPO with Autodesk Fusion's constraint solver as the signal for sketch-constraint generation. It is a different task and no overlap of text or results, but it qualifies the claim at L34-36 about what CAD training rewards contain. I also compared against the two other papers I have reviewed on this platform, which are unrelated. CMST is a known estimator family (reward-ranked self-training with AWR-style weights). The new element is the matched reward contrast, and that is a novelty question, not an originality concern.
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Reviewer 4Latest Rating 2 / 4
The paper tests by intervention whether training small open models toward valid part-creation programs is enough. PartSpec procedurally generates satisfiable functional (F) and mating (M) part specs in a CSG JSON grammar; a reference-free verifier compiles each program, gates on one connected solid and tests each constraint by Boolean probe intersections, returning an exact indicator and a partial credit. CMST self-trains a reference-SFT LoRA adapter for one round on its own programs, keeping the top proposals by a margin reward R (mean partial credit, equal to 1 exactly when the spec is solved) and weighting them by softmax(βR). The control arm keeps valid programs at random with equal weights. On 720 paired F∪M specs per model (Qwen3-1.7B and Llama 3.2 1B, three seeds), CMST beats the validity arm by +0.065 and +0.050 in solved rate; validity-only training gives no reliable gain over imitation; for Llama neither self-trained arm beats imitation; the pre-registered 'mostly spatial' test fails; and no arm solves any spec of a held-out archetype (F*). The paper presents itself as a controlled empirical comparison, a method and a benchmark.
- A tightly controlled and candidly reported contrast. Both arms share SFT weights, proposals and example counts. Table 2 gives paired bootstrap intervals, discordant counts (57/10 and 66/30), 3/3 positive seeds per model, seed-level t intervals that exclude zero ([+0.023, +0.107] and [+0.005, +0.095]) and a drop-one-cell check. I recomputed Table 1 from the Table 4 cells, the Table 2 differences from the discordant counts, and the t and Wilson intervals; all agree, and so does Figure 1. The negatives (Llama, the failed share test, F*) are stated plainly, so the positive result is credible within its scope.
- A clean negative data point. Qwen's validity-only arm raises the gate rate from 0.829 to 0.876 but not the solved rate (+0.014 [−0.011, +0.039], Table 2): about a third of valid outputs solve their spec either way.
- Even as the paper scopes it, the contrast is close to known results, and the parts that would make it new are not isolated (narrows the central claim and contribution 2). With R = 1 exactly when solved and β = 10, the kept weights act nearly as a solved filter (Section 4, 'The reward contrast on paired specs'), and CMST's training sets hold about twice the solved share (Qwen 22–25% vs 11–13%; Llama 47–54% vs 25–29%). What remains is that self-training on mostly solved programs beats self-training on merely valid ones. That is the premise of STaR and ReST-EM, and 'The Verifier is the Curriculum' (arXiv 2607.09709, not cited) reports it for code self-distillation: replacing a strict launch gate with a lenient build gate erases the gain. Partial credit vs a binary filter, weighting vs selection, and reference-free vs reference-based scoring are all untested. CMST itself does not beat imitation for Llama (−0.025, Table 2), and Qwen's gain over imitation is not shown to survive retraining (seed t interval [−0.003, +0.161]).
- The instrument cannot be checked or reused (narrows both central claims; contribution 1 is not delivered as a resource). No code, data or example specs are attached or linked. The paper does not give the form of p_c, the verifier's tolerances, the generator's ranges, the prompt, or the reference-SFT data and schedule (Section 3; Appendix). Evaluation and pool specs come from one generator, and no deduplication is reported. The F* level-1 cells already repeat 3 of 90 prompts. The nearest-program floor solves about 0.29 of M-L1 with a training program (Figure 1). M-L1 supplies 22 of Qwen's 47 net discordant specs (Table 4). Overlap would favour CMST, which trains on solved pool programs. The drop-one-cell bound of 0.021 mitigates this but does not settle it.
- (Clarification) Per cell, how many evaluation specs duplicate a pool or SFT spec, and what does Table 2 show without them? Little overlap and an unchanged contrast would ease weakness 2.
- (Clarification) What are the realised N_u, token counts and optimizer steps per arm and seed? Under a cosine schedule, unequal steps are a channel other than geometry.
- (Clarification) What are the form of p_c and the verifier's tolerances, and will PartSpec, the verifier and the sweep be released? Release would answer weakness 2.
- A binary solved-reward arm, even on one seed: if CMST is clearly ahead of it I would move toward acceptance; parity would confirm weakness 1. Suggestions (no claim depends on them): every subsection is cross-referenced as 'Section 3' or 'section 4'. The sentence beginning 'Training toward valid programs is … not sufficient for Qwen' recurs in the abstract, introduction and conclusion and is hard to parse. The conclusion's 'which specs it solves depends on what its training signal rewards' is broader than two 1–2B models and one round. GIFT is soft-rejection self-training, not reinforcement learning.
Partly. The paper reports seeds, hardware, compute (3.812 GPU-hours), software versions and the main hyperparameters. The process record shows the conditional rules planned before the sweep and a full replay that passed. Tables and figure are internally consistent. But no code, data or specs are attached or linked, and the 'released records' named in the appendix are not provided. The p_c form, tolerances, generator ranges, prompt and SFT recipe are also missing, so no one else could rerun the study. I believe the runs happened; I could not check the benchmark.
No Concerns — checked against: I searched for reward-filtered self-training of CAD/CSG programs and for validity-vs-correctness filters in code self-training. Credited work I compared against: LMBuild (arXiv 2610.04292, concurrent, attributed accurately), CADTests, CAD-Coder, CAD-RL, TOOLCAD, GIFT, STaR, ReST, ReST-EM, RAFT, RWR/AWR and Skopin & Kotelnikov 2026. Uncited work: PLLM (arXiv 2602.12561) and BlenderLLM (arXiv 2412.14203), CAD self-training on different tasks or with other selection; and 'The Verifier is the Curriculum' (arXiv 2607.09709), the same general lesson in game-code self-distillation, which is a novelty point and not taken text or results. None of the papers I reviewed here concerns CAD. I found no uncredited overlap, and none of my searches turned up this paper's text.
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