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Paper summary
This paper proposes Group-Balanced Supervised Fine-Tuning (GB-SFT), a simple yet general framework that redistributes the supervised loss budget across semantically meaningful token groups to emphasize knowledge payload (e.g., answers/values) over scaffolding tokens (e.g., citations, template prose) in knowledge-intensive domains. The authors unify standard SFT, class-balanced, and span-balanced objectives in a two-parameter family that controls class- and span-level budget splits, provide a concise analysis characterizing how the loss moves with these parameters, and validate the approach on four legal/medical benchmarks with new, contamination-controlled datasets. Empirically, GB-SFT consistently improves knowledge injection over strong token-level reweighting baselines and group-robust optimization, while preserving scaffold knowledge (e.g., citation recall) better than masking-based controls.
Critical strengths
- The paper clearly reveals that standard token-level SFT can allocate an excessive portion of the loss budget to long scaffold tokens, which is an interesting observation that may attract further research attention.
- The paper proposes GB-SFT, a simple yet effective method. Experiments across multiple datasets and models show that it consistently improves performance over strong baseline methods.
- The authors conduct experiments from multiple perspectives and demonstrate significant performance improvements over the baselines.
Critical weaknesses
- GB-SFT achieves clear improvements, but its core loss formulation is relatively similar to existing class-balanced weighting methods. The authors are encouraged to further clarify the fundamental differences between GB-SFT and traditional class-balanced loss.
- The experiments suggest that the method depends on accurate semantic grouping. For example, the performance of automatic grouping drops noticeably on NC-REAL, which may limit its applicability to general SFT data.
- The main results are still largely based on ranking metrics, while the accuracy under free-form generation is much lower. It would be helpful for the authors to further discuss this gap.
Questions for authors
- If the training data does not contain explicit payload/scaffold annotations or semantic group labels, how can GB-SFT be applied in practice?
- Why does GB-SFT achieve very high performance on the ranking metrics, while the success rate under free-form generation remains relatively low?
4 comments
Part 2/2: Grouping accuracy; the practical importance of our problems and groupings; ranking vs. generation
On dependence on accurate grouping (W2, Q1). The NC-Real drop in automatic labeling accuracy is instructive to explain, because its mechanism is not what the error rate suggests. Relocating a fraction of gold payload spans under random corruption costs almost nothing out to p = 0.5, where the arm still captures 95–100% of the gold gain. A prompted tagger erring at p = .293, a rate the corruption curve says is free, nevertheless lands at ungrouped SFT.
The difference is the structure of the error. The tagger returns a well-formed value of the right type in the right position ("ten days" where gold reads "$12,480"), which the model takes seriously; random relocation produces incoherent groups it ignores. The operative condition is not label accuracy but whether a wrong guess is also plausible. We will state that as a testable precondition.
On availability more broadly, which all three reviews raise: in law and medicine the output format is mandated, not chosen (e.g. published citation grammars, regulation-structured drug labels, required clinical schemas) and the same regulation that creates the scaffold is what makes the payload locatable. The grouping is a property of the domains where the pathology is worst rather than a convenience we selected for. We did not write these templates: Housing-QA is an external published benchmark of real U.S. landlord–tenant law, so the 81.4%/5.1% split measures how those documents are written, and NC-Real and OpenFDA substitute counterfactual payload values into real statutory and real FDA-label carriers as contamination control requires.
One half of grouping selection is free: at α = 0 each class takes 1/K regardless of class masses, so granularity fixes the budget with no labels. Testing a labeler's error structure, though, required gold labels, and we have no gold-free prospective test to offer. Where groups come from without annotation: Housing-QA's citations from a citation grammar, OpenFDA's dose fields from structured source labels, Tulu's classes from Python's tokenize module, and GSM8K's payload boundary from the dataset's own #### delimiter.
On ranking versus free-form generation (W3, Q2). Teacher-forced ranking is the standard instrument in the knowledge-editing literature. We report both ranking and free generation, which is why the gap is visible in our paper.
On NC-Real the teacher-forced overwrite rate is .9544 against .190 in free continuations: roughly five-fold overstatement. We emphasize, however, that the ordering is preserved, and GB-SFT still emits the taught value about 4× as often as SFT.
We can now say why the generation rate is low, which we think is the more useful answer to Q2. The gap is knowledge-limited, not decoding-limited: constraining decoding to emit a well-formed citation does not raise the rate (it scores .560 against .580 for ordinary greedy decoding). If the model were failing to express a payload it had learned, forcing the surface form would help; it does not. The payload is not yet learned robustly enough to be retrieved under the model's own decoding.
That points to a corpus-level remedy rather than a loss-level one, of the kind Allen-Zhu & Li (2024) identify: a fact becomes extractable once it appears across sufficient paraphrase and format diversity. It is orthogonal to how the loss is weighted, and we would not expect a different weighting to close it.
Closing the gap plausibly needs a corpus-level intervention of training on contexts that elicit the payload, not only on the payload itself. We leave this as future work and note that it is a particularly exciting direction. As is, our ranking improvements are measured on the instrument the memory-editing literature uses to establish its own claims, and the generation results point the same way.
We thank the reviewer for their careful attention and valuable feedback. For convenience, all substantial new content from the discussion period is in App. E of our updated paper.
Response to the Authors
I appreciate the authors' thorough response. The provided explanations have resolved my initial concerns.
Follow-up: additional findings support your positive framing
Thank you! We’re glad the explanations resolved your concerns. We also appreciated the framing in your initial review: describing the budget-allocation observation as something that “may attract further research attention” is exactly how we hope the work is read.
The revision adds a result that speaks to that generality. On the grade-school math benchmark GSM8K, the loss budget turns out to be a monotone lever on safety-guardrail erosion, a behavior that is not part of the training objective at all (App. E.6). We think you’ll appreciate the greater applicability of our work already being apparent.
Your review noted minor or fixable concerns about soundness, which we believe the revision now resolves. If you agree, we would be grateful if you would consider whether a stronger assessment is warranted.
Part 1/2: The observation generalizes further 🙂 ; clarified relation to class-balanced loss
We thank the reviewer for the careful summary, which states the contribution exactly as we intend it. We are glad the budget-allocation observation reads as "an interesting observation that may attract further research attention": that is the framing we hoped for, since we regard inspiring further work on the problem as the durable half of the contribution and the objective as one way of acting on it. We are glad too that the method read as simple and effective across datasets and models.
The observation generalizes further than the paper claimed. We think this is the most useful thing we can report back, because it speaks directly to the framing you gave the work.
If budget misallocation is a general property of token-summed cross-entropy rather than an artifact of the corpora we built, it should govern outcomes we never set out to measure. We tested that during the discussion period on GSM8K, a math corpus we did not construct, whose grouping is free because the payload boundary is the dataset's own delimiter. We found that GB-SFT improved a behavior that is not knowledge at all: the model's tendency to refuse harmful requests.
Ordinary SFT drops harmful-prompt refusal from 95.5% to 81.0% (LLM-judged, five seeds, 420 prompts). The erosion is monotone in the budget parameter (81.0 / 82.9 / 85.7 / 89.2 as α goes 1.0 → −0.5, Cochran-Armitage trend z = 7.48) and α = 0 retains about a third of what SFT loses, at matched task accuracy (67.4% against 68.4%). This is not a uniform rise in reluctance: false refusal on 350 benign prompts rises far less than refusal on harmful ones, so the separation between the two improves from 73.7 under SFT to 77.9 which is above the aligned checkpoint fine-tuning started from. So the loss budget governs what fine-tuning damages as well as what it acquires, on a corpus, a grouping source and a metric all outside the ones the paper was built around. We think that is the strongest available evidence that the budget-allocation observation is a durable part of the contribution. The conditions bind in both directions: Alpaca's 98/2 payload split would have an equal-budget objective upweight boilerplate instead, and a corpus that erodes refusal in one model need not erode it in another. App. E.7 of the revised paper gives the full scope analysis.
The three weaknesses raised are three points we would ourselves flag as worth clarifying. We take W1 here, and W2 and W3 in Part 2.
On the relation to class-balanced loss (W1). The family is deliberately in that lineage and we will make the inheritance explicit, including that Cui et al.'s own β is already a continuous knob that corresponds structurally to our α. The substantive difference is that classification admits an equivalent post-hoc correction and we do not. Logit adjustment, balanced softmax and Elkan-style thresholding exist because classification has a final argmax over the grouped variable and a test-time group prior to correct. Neither holds here: a token's semantic class is not the prediction target and is unknown at inference. A model emitting 2% citation tokens at test time is correct, not biased.
We will also pre-empt Byrd & Lipton (2019): in an autoregressive loss the terms share not only parameters but conditioning, so a down-weighted span is still generated at inference and still conditions every token after it.