acceptodds
Under review as a conference paper at ICLR 2027

The Durable Asset Is the Data, Not the Weights

Abstract

Organizations increasingly serve fleets of fine-tuned specialists on open-weight language models whose bases improve every few months. Each release reopens the same decision: freeze the old specialist, port its weights, refresh it from retained behavior, or retrain. These strategies form a ladder of retained resources—nothing, weights, inputs, labels—yet the decision has never been measured: prior work evaluates ad-hoc model pairs, never a real release sequence. We measure it longitudinally, on a complete fourteen-month release lineage (four consecutive generations, two scales, six tasks spanning classification, structured generation, and tool use), validated on a second family with fully documented training genealogy; hypotheses are fixed before each experimental wave, and every comparison is paired, per-example, and cost-accounted. We find that (1) specialization is durable: a frozen specialist can outperform the newest base for over a year, governed by a measurable task–base coupling rather than task class; (2) weights are fragile: porting between architecturally identical checkpoints from independent pretraining runs collapses below the no-adapter floor, yet porting onto a short continued-pretraining descendant is nearly free—portability is a distance budget in pretraining tokens, not an architecture or family property; and (3) data recovers what weights cannot carry: distilling the old specialist into the new base, using retained inputs only, matches gold-label retraining with zero new annotation. A pre-specified policy built on these facts nearly matches always-retraining at a third of its cost with zero regressions, while the shape-compatibility rule practitioners use is the worst policy we test. All code, records, and cost logs are released; everything runs on one consumer GPU.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Parameter-efficient fine-tuning, Base-model upgrades, Fine-tuning transferability, Knowledge distillation, Longitudinal benchmark

Reviews

Among:
Shape:
1234this paper, Bottom 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_3GzvOpenReview ↗
Rating
2(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2(+1)
Read review
Paper summary

The paper studies how to maintain a task-specific model when its base model changes. It compares keeping the old model, copying its adapter, distilling its predictions, and retraining. Experiments cover four Qwen generations and selected OLMo checkpoints. The paper also proposes a policy for choosing when to update and reports lower training cost.

Critical strengths
  1. The comparison across model versions addresses a practical problem. It measures task quality, prediction changes, and update cost together. This gives a useful picture of the choices available when a base model is replaced.

  2. The OLMo tests control for template, precision, and output format. They show that matching architectures alone do not guarantee successful adapter transfer.

Critical weaknesses
  1. The cost claim depends on how the reference model is obtained. Algorithm 1 uses the fully retrained target model's score to decide whether retraining can be skipped. Table 4 reports 15.6 versus 47.7 GPU-hours, but it is unclear whether reference training and rejected candidates are included. Without these costs, the saving may be overstated.

  2. The broad claim about weights and data goes beyond the tested baselines. The paper mainly tests direct adapter copying, without alignment methods such as Cross-LoRA [1]. Trans-LoRA [2] already studies transfer through distillation. The refresh experiments also cover only one Qwen upgrade, which limits the general conclusion.

Questions for authors
  1. How is the reference score obtained, and does Table 4 include all costs needed to make the update decision?

  2. Does an alignment-based transfer method change the result on a model pair where it applies?

References

[1] Xia et al. Cross-LoRA: A Data-Free LoRA Transfer Framework across Heterogeneous LLMs. 2025.

[2] Wang et al. Trans-LoRA: towards data-free Transferable Parameter Efficient Finetuning. 2024.

2 comments

Q1. How is the reference score obtained, and does Table 4 include all the costs needed to make the update decision?

Your reading of Algorithm 1 is correct, and Table 4 did not include those costs. The 15.6 GPU-hours counted only the actions that were finally selected. Evaluating the decision branches requires the retrained reference in all 33 episodes; one episode also reaches the REFRESH test, and that candidate was selected. FREEZE and PORT candidates need no training, so there are no other rejected candidates with a training cost. Charging the references once each, plus that student, gives 50.7 GPU-hours and 33 gold-label episodes, against 47.7 and 33 for always retraining. These are migration-training costs only; scoring, serving and data management were outside the accounting in both columns. The cost-saving claim is withdrawn.

Q2. Does an alignment-based transfer method change the result on a model pair where it applies? The refresh experiments cover only one Qwen upgrade.

We have no matched Cross-LoRA or Trans-LoRA result, so whether alignment changes the picture on these pairs is an open question that we will state as such. One clarification we owe you: REFRESH follows the distillation route that Trans-LoRA proposed, as §5.4 says; it differs in distilling on retained real inputs, whereas Trans-LoRA is near-data-free. We will make that relation explicit in Related Work. The failure in §5.3 is specific to copying adapters directly across the independent runs we measured. The REFRESH results come from one Qwen upgrade (CLINC150 extends it to a second task class on the same hop) and from teacher-seen inputs, so they cannot establish a general ordering of weights, data and learned transfer methods, and we will narrow the claim accordingly.

Changes 1, 3, 6 and 8 cover this review.

Thanks for the clear response and revision. Since the main soundness error is now fixed, I am raising my rating from 1 to 2.

Two concerns remain (also noted by Reviewers vRfP and KMAA):

  1. With the cost-saving claim withdrawn, the one-hop coupling forecast negative, and REFRESH limited to teacher-seen inputs, the remaining result that naive copying fails across independent runs while freezing, retraining, or distilling works is largely expected.
  2. No alignment or learned transfer baseline was tested, so it remains open how much of the porting gap existing transfer methods would close.

Overall, I think a rating of 2 accurately reflects the quality of the current manuscript.

Reviewer_KMAAOpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
2
Soundness
3
Read review
Paper summary

The authors compare performance of specialists based on older, weaker models to various “upgrades” that adopt a newer, stronger model of the same family. These upgrades correspond to the required resources retained between specialist versions (weights, inputs, input/label pairs). They establish that porting the same adapter weights onto a stronger model is ineffective while training with the associated data can produce stronger specialists, and present results with two model families.

Critical strengths
  • Addresses a practical problem with deployment of specialized models (namely, that the underlying base models become obsolete relative to the capabilities of newer models)

  • The authors define “upgrade” options in terms of required resources, a practical yardstick

Critical weaknesses
  • The prose is occasionally difficult to follow. Additionally, the paper should better orient itself relative to prior transfer literature to clarify why “port” without additional training is one of the upgrade options studied. The floor and ceiling/reference baselines should also be made clearer earlier in the paper.

  • The authors should better clarify when each option should be considered (v. what options are strictly dominated in performance and cost). E.g. in a regime where you are able to do some additional fine-tuning, “freeze” may not be the optimal action, but “freeze” can dominate “port” in lower resource settings. They address this for refresh v. retrain, but not the freeze and port options.

  • The result that data can recover performance where porting weights cannot is not surprising. In particular, it is not surprising that prompts that have been shown to be effective in previous training, especially when paired with distillation from the old specialist, would be effective. The analysis of how quickly the performance of porting the model weights degrades is potentially a more useful analysis and should be a greater focus of the paper.

Questions for authors
  • Is “porting” commonly performed without any additional training? This appears to be nearer to a baseline for comparison than a usable approach.

  • How does this compare to the performance of the discussed prior transfer methods?

2 comments

The prose is occasionally difficult to follow; the paper should orient itself relative to prior transfer literature and define the floor and reference baselines earlier.

Agreed on all three. §3 will open with the floor (the new base prompted without a specialist) and the reference (the new base retrained on gold labels, which is an empirical reference that another method could exceed, not a ceiling), followed by a short paragraph on why PORT is studied at all and a decision table. We will also rewrite the passages that were hard to follow.

Q1. Is porting commonly performed without any additional training? It looks closer to a baseline than to a usable approach.

We think of it as both. PORT is the one way onto the new base that costs no training, and it is what an operator can try whenever the adapter shapes match; serving stacks check shape compatibility, not release lineage, which is why we evaluated it as a policy in Table 4. We have no survey of how often people actually do this. What we can say is that FREEZE, which is also free when the old base can still be served, beat direct copying in all nine task/scale cells on the Qwen2 to Qwen2.5 hop, and that copying was competitive only on a short continuation. The decision table will make clear where PORT is dominated.

Q2. How does this compare to the performance of the prior transfer methods discussed?

We cannot report that comparison, because we did not run any learned alignment or synthetic-data transfer method. What the paper can compare is what each rung requires: REFRESH needs the old teacher and the retained inputs, RETRAIN needs gold labels. §3 will state this before the results, and the headline will be limited to the reuse strategies we measured. The result that data recovers what ported weights cannot is not surprising; the analysis of how quickly ported weights degrade deserves more focus.

We agree that recovery from data is expected. The quantities we think are worth having are the retention and horizon per hop and the porting-decay curve along the OLMo spectrum in §5.3, and we will give the latter more room, with the unmeasured settings listed explicitly. Changes 5, 6, 7 and 8 cover this review.

Thank you for the response and revisions, which have improved the work. I remain concerned about whether PORT is commonly used/expected to perform in practice and by the lack of comparison to prior methods. With these concerns, I retain my score of 2 for the current draft.

Reviewer_vRfPOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies how to maintain task-specific language models as new base models are released. The authors compare freezing old specialists, directly transferring LoRA weights, distilling into new bases, and retraining. They evaluate these strategies across several model generations and tasks, and propose a cost-aware model upgrade policy.

Critical strengths
  • The paper addresses a practical problem in maintaining fine-tuned models across base-model updates.

  • I appreciate the systematic evaluation across model generations and tasks.

Critical weaknesses
  1. I am not fully convinced of the novelty of the main findings. For example, in Sec. 5.1, an older fine-tuned specialist outperforming a newer model without task-specific fine-tuning is not particularly surprising. Similarly, improvements in tasks such as text-to-SQL may reflect the growing capabilities of newer base models. The proposed task base coupling mainly describes these observed differences, but its additional value remains unclear to me.

  2. The LoRA portability results also seem largely consistent with existing understanding. LoRA updates are learned for a specific base model, so directly applying them to independently trained weights is not expected to work reliably, even with the same architecture. Prior work such as [1] has already addressed this issue. While the continued-pretraining experiments are useful, I am not sure they support the broader claim that weights are inherently less durable than data.

[1] Wang et al. "Trans-LoRA: towards data-free Transferable Parameter Efficient Finetuning." NeurIPS 2024.

Questions for authors
  1. Can task–base coupling predict future upgrade outcomes rather than just describe past results? For example, could the authors estimate it from earlier releases and test its predictions on a held-out release?

  2. Could the authors compare naive LoRA porting with an existing transfer method, such as Trans-LoRA, on at least one representative model pair? This would help clarify the contribution beyond the known limitations of direct weight transfer.

2 comments

On novelty: an older fine-tuned specialist beating a newer base without task-specific fine-tuning is not surprising, and coupling mainly describes the observed differences.

We agree that the direction is what one would expect. What we think the paper adds is the size and the horizon of the effect, and the fact that it is not uniform across tasks: on Spider, where the coupling is high, freezing retains only 41–93% of the attainable gain per hop (mean 64%), whereas xLAM's advantage actually rebounds at Qwen3, from +2.6 to +5.1 points. We will rewrite the contribution statement around those measurements rather than around the direction, and present coupling as a descriptive summary (changes 2 and 7).

Q1. Can coupling predict future upgrade outcomes rather than describe past ones?

We tried, retrospectively, and the honest answer is no. For the 18 episodes that have an earlier hop for the same task and scale, we predicted the reference gain on the new base from the previous hop. In nine episodes we could estimate the previous ratio of reference gain to floor gain and apply it to the observed change in the prompted floor; in the other nine we could only carry the previous reference gain forward. Comparing the predicted gain on the gate half with the realized retrain-minus-freeze gain on the held-out half gives a Spearman correlation of 0.15, and the sign agrees in only 9 of the 18 episodes. So coupling describes what happened on past upgrades, and we have no evidence that it forecasts the next release. §5.6 will report this as a negative result.

Q2. Could naive LoRA porting be compared with an existing transfer method such as Trans-LoRA on at least one model pair?

We did not run Trans-LoRA, and we do not want to imply that PORT competes with it. Trans-LoRA trains a new adapter on the target base by distillation; PORT asks what happens when the old adapter is copied with no training at all. The contrast we actually measured is between independent pretraining runs and short continuations of the same weights. We will say in the paper that the experiments do not rank PORT or REFRESH against Trans-LoRA, that they do not support a broader claim that weights are inherently less durable than data, and that "weights are fragile" refers only to the measured contrast. We will also position both rungs relative to Trans-LoRA and Cross-LoRA in Related Work.

Changes 2, 6, 7 and 8 cover this review.

Thank the authors for the clarification. I appreciate the authors' willingness to clarify and narrow the claims.However, my main concerns remain. The new results suggest that task base coupling has little predictive value and the clarification on LoRA portability does not fully address my novelty concern.

While the measurements are useful, I am still not convinced that the paper offers enough new insights to meet the ICLR bar. I will therefore maintain my overall rating of 2 (Weak Rejection).

Reviewer_qYbSOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies how organizations should update fine-tuned specialists when a newer base model is released. It measures four upgrade strategies that form a ladder of retained resources: freeze the old specialist, port its weights, refresh it by distillation on retained inputs, or retrain on gold labels. The measurements follow a complete Qwen release lineage longitudinally, are validated on OLMo, and test hypotheses fixed before each experimental wave.

Specialization is durable: frozen specialists can outperform newer bases for over a year when task–base coupling is low, but erode quickly when it is high. Weights are fragile: porting fails between independent pretraining runs of identical architecture but is nearly free across short continued pretraining, so portability depends on pretraining distance rather than architecture. Distilling the old specialist on retained inputs matches gold-label retraining without new annotation. A pre-specified policy built on these findings nearly matches always-retraining at a third of its cost.

Critical strengths

[C1] Careful experimental design. The hypotheses for each experimental wave are fixed before the wave is run, and the paper reports the ones that were refuted, including the authors' own prediction that adapters would port well between architecturally identical models. All comparisons are paired on the same test sets and tested with exact McNemar tests and bootstrap confidence intervals. Parity claims are backed by non-inferiority tests, and the porting failure is checked against simple explanations such as a chat-template mismatch, 4-bit quantization and output parsing.

[C2] A clear and practically useful result on porting. Copying a LoRA adapter between architecturally identical checkpoints from independent pretraining runs (Qwen2 to Qwen2.5) is worse than keeping the old specialist in every case tested, and on Banking77 it is even worse than the new base model with no adapter. In contrast, copying it onto a continued-pretraining descendant (Qwen2.5 to Qwen2.5-1M) loses almost nothing. The OLMo experiments, where the training history of each checkpoint is documented, show the same pattern.

Critical weaknesses

[W1] The REFRESH result does not show that the old specialist's behavior can replace the gold labels. In the REFRESH experiment, the old Qwen2.5 specialist relabels the training and validation inputs of each task (Appendix I). Most of these are the same inputs it was fine-tuned on with gold labels. On the training inputs its labels agree with the gold labels 97.45% of the time on Banking77, 88.3% on Spider (exact string match) and 92.8% on xLAM. On the validation inputs, which it was not trained on, agreement drops to 92.6%, 66.8% and 83.4%. The new student is therefore trained largely on the original gold labels, so it is not surprising that it matches gold-label retraining (retention 0.997, 1.047 and 0.960).

This setting does not match the use cases the paper gives for REFRESH in Section 5.4. One is specialists trained from preference or feedback signals, for which no labeled dataset exists. The other is specialists obtained without their data. In the first case the teacher was never fit to gold labels, and in the second there are no retained inputs to relabel. For the same reason, the label-budget comparison on Spider in Appendix E is not a fair one. There, gold-label retraining needs more than 4,096 labels to reach 95% of the gain, while REFRESH reaches 105% with no new labels; but the REFRESH teacher was itself trained on the full gold-labeled training set. Running REFRESH on inputs the teacher was not trained on would show whether the result holds.

[W2] The cost of the proposed upgrade policy appears to be under-counted. The paper claims that its policy (Algorithm 1) nearly matches always retraining at about a third of the cost (Table 4). However, the first step of Algorithm 1 estimates Ot(bj)O_t(b_j), the score of a specialist retrained on the new base, and the policy needs this score in every episode to decide whether to keep the old specialist. Computing Ot(bj)O_t(b_j) requires retraining with gold labels, so the policy should require retraining, and gold labels, in all 33 episodes, just as always retraining does. Yet Table 4 charges the policy for gold labels in only 9 episodes and 15.6 GPU-hours, against 33 episodes and 47.7 GPU-hours for always retraining. The paper does not explain how Ot(bj)O_t(b_j) is obtained without retraining, so the reported savings may not be achievable in practice.

Questions for authors

[Q1] In the policy replay (Table 4), how is Ot(bj)O_t(b_j) obtained in each episode? Is the cost of the retraining included in the policy's 15.6 GPU-hours and 9 gold-label episodes?

[Q2] Can you run REFRESH on inputs the teacher was not trained on? For example, train the teacher on part of the training split and relabel only the remaining part, then report teacher–gold agreement and the student's retention.

[Q3] The claim that portability depends on continued-pretraining distance rests on two distances (46B and 2.9T tokens) from a single OLMo checkpoint, two intent-classification tasks and rank-16 adapters. The size of the porting loss also depends on adapter rank: on the Qwen2 to Qwen2.5 hop, the Banking77 loss shrinks from 50 to 21 points at rank 64. Can you add intermediate distances, at least one non-intent task, and a higher-rank or full fine-tuning setting?

[Q4] Table 2 describes Qwen2.5-7B-Instruct-1M as a continued-pretraining descendant of Qwen2.5, but it seems to be continued from the Qwen2.5 base model and then post-trained separately (https://qwen.ai/blog?id=qwen2.5-1m)? In the second case, this hop also changes the post-training, not only the amount of continued pretraining.

1 comment

Thank you for a review that found two real problems. Both are acknowledged in the general response; here we answer your questions in order.

Q1. How is O_t(b_j) obtained in each episode, and is the cost of that retraining included in the policy's 15.6 GPU-hours and 9 gold-label episodes?

It is obtained exactly the way you suspected: we retrain the specialist on the new base and score it on the gate half. Its cost was not included. We charged training only when RETRAIN was the action finally chosen, which is wrong, because the gate needs the score in every episode. With the reference charged everywhere, the policy costs 50.7 GPU-hours (47.656 for the references and 3.086 for the one REFRESH student that reached the gate, at the replay's convention of 0.9 times a retraining run) and needs gold labels in all 33 episodes, against 47.7 GPU-hours and 33 episodes for always retraining. We withdraw the cost claim. The decisions and their held-out quality do not change (0.37 points mean regret and zero regressions, against 0.21 and one), but the policy no longer saves anything.

Q2. Can you run REFRESH on inputs the teacher was not trained on?

We agree that this is the right experiment, and we have not run it. The numbers you cite point the same way we now read them: on Spider the teacher agrees with gold on 88.3% of training inputs but only 66.8% of validation inputs, so distilling on inputs the teacher never saw would very likely transfer less than the retention of 1.047 we measured on retained inputs. You are also right about Appendix E. Its gold-label curve counts only new annotation, while the teacher had already benefited from the full labelled set, so the comparison is not a fair one. We will say so next to every REFRESH result, and the two §5.4 use cases are withdrawn (item 2 of the general response).

Q3. Can you add intermediate distances, at least one non-intent task, and a higher-rank or full fine-tuning setting?

Not within the discussion period. What we have is the controlled OLMo comparison on two intent tasks with rank-16 adapters at two continuation distances, roughly 46B and 2.9T tokens, plus the observation on the independent Qwen hop that going to rank 64 shrinks the Banking77 porting loss from about 50 points to 21. Intermediate distances, a non-intent task along the OLMo trajectory, and a higher-rank or full fine-tuning sweep are all unmeasured, which means the paper cannot locate a general token threshold. §6 will say this explicitly.

Q4. Qwen2.5-7B-Instruct-1M seems to be continued from the Qwen2.5 base model and then post-trained separately.

You are right, and thank you for checking. Our source adapter was trained on Qwen2.5-7B-Instruct, and the Qwen2.5-1M technical report describes long-context continued pretraining from the base model followed by its own post-training. The two Instruct releases therefore cannot isolate continued-pretraining distance, and Table 2 should not present them as if they did. The same-run OLMo checkpoints in §5.3 are the controlled comparison.

Changes 1, 3, 4 and 7 in the general response cover this review.

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

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