Trading Parameters for Accuracy in MambaVision for Chest Radiograph Classification
Qaiser Farooq
Abstract
MambaVision, a hybrid state-space and attention
backbone, places most of its parameters in its widest, fourth
stage. We quantified what that stage contributes to multi-label
chest radiograph classification. The fourth stage was replaced
with lighter single-scan state-space blocks adapted from Spatial-
Mamba, with multi-scale dilated depthwise convolutions applied
to the scan output; the first three stages were retained. Tiny,
Small, and Base models were evaluated across nine dataset–
scale combinations drawn from two source cohorts: the National
Institutes of Health ChestX-ray14 archive (full ChestMNIST and
a high-resolution subset) and Indiana University Open-i. At the
Tiny scale, replacement reduced parameter count by 35.7%
and increased graphics processing unit throughput by 19.3%;
the savings came from the stage’s dense projections, not from
removing quadratic attention. Without distillation, the mean area
under the receiver operating characteristic curve on ChestMNIST
was 0.004 lower than the baseline (95% bootstrap confidence
interval, 0.002 to 0.006), and 0.003 to 0.006 lower across all nine
combinations. Knowledge distillation from an unreplaced teacher
narrowed the gap to the undistilled baseline to 0.001–0.002 and
met the equivalence criterion on ChestMNIST, but distilling the
baseline with the same recipe improved it by 0.001–0.003, so a gap
of 0.002–0.005 persisted under symmetric training. At the Base
scale, the unreplaced Small model was both smaller and more
accurate. Fourth-stage replacement is a useful trade-off only for
Tiny and Small models. These measurements let developers of
chest radiograph screening tools weigh model size and speed
against a quantified loss of diagnostic discrimination.
Review reports
xPeerd (AI review)
AI Review (xPeerd — DAReview)
Summary
This manuscript evaluates whether the parameter-heavy fourth stage of MambaVision can be replaced by lighter single-scan state-space blocks, adapted from Spatial-Mamba, for multi-label chest radiograph classification. The paper is technically ambitious, generally well organized, and explicit about the engineering trade-off it investigates: reduced parameters and improved throughput at a measurable loss in Macro-AUC. The title, abstract, introduction, and conclusion are well aligned on the core claim that stage replacement is useful mainly at Tiny and Small scales, not at Base scale .
The main strengths are the controlled ablation design, explicit reporting of computational trade-offs, and the authors’ effort to test symmetric knowledge distillation rather than claiming gains from a one-sided protocol . The main weaknesses are limited external validation, dependence on noisy NLP-derived labels, partial cohort non-independence, and a clinically thin justification for the chosen equivalence margin and deployment implications . I do not see strong signs of fabrication or paper-mill style incoherence; the manuscript is internally coherent, hypothesis-driven, and numerically self-consistent across the retrieved sections. However, some claims of practical significance would benefit from tighter clinical grounding and stronger reproducibility detail.
Potential Major Revisions
- Clinical significance is asserted more strongly than clinically validated evidence supports.
The abstract states that “Fourth-stage replacement is a useful trade-off only for Tiny and Small models” and frames the losses as quantified engineering trade-offs for screening tools . In the discussion, the paper further interprets the Tiny-model drop as “about eight fewer detected findings per 1,000 positive findings” and suggests that the method “suits high-volume retrospective screening better than settings where each missed finding is costly” . Yet the same limitations section concedes that the ±0.005 equivalence margin is “itself a methodological rather than clinically validated threshold” . This creates a tension between the strength of the deployment-oriented interpretation and the admitted lack of clinical validation of the decision threshold underlying equivalence.
The manuscript should either soften these practical claims or support them with a clearer clinical rationale. As written, the engineering evidence is reasonably strong, but the clinical framing is somewhat overextended relative to the evidence presented.
- Dataset independence and generalizability remain materially limited.
The manuscript explicitly states that the nine evaluation cells come from “two source cohorts rather than three” because “ChestMNIST and the NIH subset share equipment, demographics, and NLP label noise” . It also acknowledges that “70.0% of NIH-subset test images are in the ChestMNIST training split,” and that Indiana has “up to 8.9% potential repeat-patient overlap” . These are important limitations. Although the paper is transparent about them, the result is that claims about robustness across “nine dataset–scale cells” may read more broadly than the evidence warrants.
The manuscript would be stronger if it reframed this as repeated evaluation under partially shared data-generating conditions rather than implying near-independent replication across nine cells. External validation on a genuinely disjoint cohort, which the authors mention as future work via MIMIC-CXR, is needed before broader performance or deployment conclusions can be considered secure .
- The novelty is mostly a targeted engineering adaptation rather than a broader methodological advance, and this should be positioned more carefully.
The contribution section claims “A controlled evaluation of Stage-4 replacement” and “an analysis across nine dataset–scale cells” with several ablations . That is a valid contribution. However, the method itself is not a fundamentally new backbone family; it is a stage replacement of MambaVision with blocks “adapted from Spatial-Mamba” while retaining stages 1–3 . The manuscript’s actual novelty lies less in proposing an entirely new architecture than in carefully quantifying where stage replacement is Pareto-favorable and where it becomes inferior.
I think the paper would benefit from making this narrower novelty claim more explicit. At present, some wording risks overstating architectural originality when the real value is the disciplined trade-off study and ablation evidence.
- Some methodological choices are justified empirically, but not fully enough for reproducibility-minded readers.
The manuscript introduces a ridge-regularized projection for Tiny-scale width mismatch: “we project the checkpoint with a ridge-regularized linear map P ∈ R512×640 (λ = 10−3)” and report that it improves early-stage metrics but not final AUC significantly after 80 epochs . This is useful, but the description is still somewhat sparse for exact reproduction. It is unclear from the retrieved sections, for example, how the activation pools are sampled in practice, whether the mapping is fit once or per run, and whether any seed sensitivity exists beyond the summary result.
Likewise, the training setup reports class-weighted BCE and KD with α = 0.5 and τ = 2.0 , and later notes sensitivity over α ∈ {0.25, 0.5, 0.75} and τ ∈ {1, 2, 4} with little effect on distilled ChestMNIST AUC . That is good, but the paper should consolidate these implementation details in a more reproducible form, especially because the contribution is an engineering trade-off study where exact settings matter.
- The argument that selective recurrence and SASF are “jointly required” is plausible, but stronger evidentiary wording is needed.
The discussion says: “Replacing the selective scan with a gated dilated depthwise block (Row B) lowers ChestMNIST AUC by 0.008… and removing SASF (Row 6) by 0.011…, so selective recurrence and multi-scale fusion are jointly required” . This is persuasive within the tested design space, but “required” is too strong epistemically. The experiments show that these components matter relative to the tested ablations, not that no alternative design at similar budget could recover performance.
I would recommend changing such language to “important within the tested architecture family” or “supported by our ablation results,” unless the authors can provide broader evidence.
- Practical performance conclusions at Base scale should be highlighted earlier and more directly.
One of the more important findings is that “Spatial-MambaVision-B (77.63M, 14.20 GFLOPs) is Pareto-dominated by the unreplaced MambaVision-S (49.38M, 7.50 GFLOPs)” and that replacement “suits only the 20M–35M hybrid regime (Tiny and Small)” . This is a strong and useful negative result. It protects readers from overgeneralizing the method. However, it deserves more prominence earlier in the abstract/introduction framing. The abstract mentions the Base-scale limitation, but the practical implication—that replacement should not be treated as a universally scalable recipe—is important enough to foreground even more sharply .
Potential Minor Revisions
- AI content analysis for this post-2021 manuscript.
The acknowledgment states: “Claude (Anthropic) and ChatGPT (OpenAI) were used for language editing only (grammar, wording, and condensing), not to generate data, results, or analyses” . Based on the prose style of the retrieved sections, I estimate a low-to-moderate probability of AI-assisted line editing, but not obvious AI-generated scientific reasoning. My estimated proportion of AI-assisted text is approximately 10%–20%, concentrated in polishing and compression rather than substantive argument generation.
Highlighted likely AI-assisted or strongly edited sections:
- The acknowledgment itself explicitly confirms AI use for editing .
- Some compact, balanced summary sentences in the abstract, such as “Fourth-stage replacement is a useful trade-off only for Tiny and Small models,” have the polished compression style often associated with assisted editing, though this is not problematic by itself .
- The discussion sentence “KD is therefore a practical way to recover baseline-level accuracy in a smaller student, not evidence that the replaced stage has zero representational cost” is rhetorically polished and may also reflect editorial assistance .
Assessed epistemic impact: low. The manuscript’s quantitative claims appear tied to tables, ablations, and explicit caveats rather than free-floating text. I do not see evidence, in the retrieved content, that AI assistance distorted the core scientific contribution.
- Typographic and style issues.
- The PDF extraction shows irregular spacing/hyphenation in several places, such as “computational effi- ciency” and similar line-break artifacts in the Index Terms area and body text. These may partly be extraction artifacts, but the final production manuscript should still be checked for hyphenation cleanliness and column-flow readability .
- Mathematical notation should be checked for consistency where operators and dimensions are introduced. For example, in the methods, the distinction between latent-state fusion before contraction and output-space fusion after contraction is important; the prose is careful, but a small clarifying diagram or notation legend would reduce reader burden .
- The statement “the two operators therefore do not commute” is correct in context, but could be followed by a one-sentence intuitive explanation for readers less comfortable with operator ordering in state-space formulations .
- The manuscript alternates between performance claims in terms of AUC, Macro-AUC, sensitivity at 90% specificity, GFLOPs, and throughput. This is appropriate, but the narrative would be easier to follow if each results subsection began with a brief reminder of the primary decision metric for that subsection.
- Formatting issues.
- Table-heavy sections appear information-dense. Table II and Table VII are valuable, but a compact visual summary of the Pareto frontier and the stage-ablation logic would improve readability, especially for readers not focused on hardware-aware model design .
- The manuscript should ensure that all acronyms are reintroduced or easy to track, especially SASF, SASSM, MHSA, KD, and TOST. In a specialized audience this is manageable, but the paper would read more cleanly with a short acronym table or a notation appendix.
- Because the paper emphasizes exact trade-offs, a one-paragraph “reproducibility capsule” summarizing hardware, seeds, training length, checkpoint initialization, and decision metrics would help.
- Language and precision adjustments.
- In the introduction, “Whether this parameter-heavy stage is necessary for thoracic radiograph classification is a practical engineering question” is fine, but “necessary” may be stronger than needed given the paper ultimately studies cost-benefit rather than indispensability .
- In the conclusion, “experiments reject a strict zero-loss H1” is statistically assertive; if retained, the manuscript should be absolutely clear that what is being rejected is the operationalized hypothesis under the tested setups and equivalence margin, not a universal proposition about all forms of stage replacement .
- The phrase “jointly required” in the discussion should be softened, as noted above .
Recommendations
-
Reframe the manuscript explicitly as a rigorous architecture-trade-off study rather than implying a broader architectural breakthrough. That positioning is more accurate and, in my view, strengthens the paper.
-
Soften clinical deployment language unless supported by clinically validated decision thresholds or external reader studies. The current engineering results are useful, but the clinical extrapolation should remain cautious .
-
Add a more detailed reproducibility block covering:
- exact initialization and fitting procedure for the ridge projection P,
- per-seed variation where custom initialization is used,
- explicit optimizer and training schedule summary in one place,
- exact code-path differences between selective_scan_fn and selective_scan_ref where relevant to reported speed/accuracy trade-offs .
-
Highlight earlier that the method is not scale-monotonic: it helps in Tiny/Small regimes but becomes Pareto-inferior at Base scale . This negative result is important and should be one of the paper’s central takeaways.
-
Strengthen the limitations section further by moving some caveats forward into the abstract or end of the introduction: noisy labels, only two effective source cohorts, overlap concerns, and lack of external validation .
-
Consider adding one dedicated figure summarizing:
- parameter reduction,
- throughput gain,
- AUC loss,
- KD recovery,
- and the Base-scale Pareto failure. This would make the manuscript’s central message immediately legible.
Overall, I judge the manuscript to be coherent, technically competent, and worthwhile, but not yet fully convincing in its broader practical interpretation. The strongest case for publication is as a careful and transparent study of when Stage-4 replacement in MambaVision is and is not a sensible efficiency trade-off for chest radiograph classification.
Reviewer3 (AI review)
AI Review (reviewer3.com)
Overview
Characterization of MambaVision Imbalance
Contribution
The authors present a stage-wise profiling of MambaVision, revealing that its fourth stage contains 58.1%–64.9% of model parameters and is dominated by dense projection operations rather than quadratic attention.
Spatial-MambaVision Stage Replacement
Contribution
The study introduces Spatial-MambaVision by replacing MambaVision's fourth stage with lighter single-scan state-space blocks featuring output-space dilated convolutions, achieving 19.7%–35.7% parameter reductions and up to 19.3% throughput gains at a quantified loss of diagnostic discrimination.
Identification of Stage-Replacement Scaling Limits
Contribution
The authors demonstrate that fourth-stage replacement provides an advantageous trade-off only at Tiny and Small model scales, as an unreplaced Small backbone Pareto-dominates the replaced Base model in both size and accuracy.
Comments (9)
1. Stage 1 resolution formula contradicts stem and Fig. 1 — Editorial
As illustrated in Fig. 1, a frontal radiograph I ∈ R H × W × 3 (grayscale replicated to three channels) passes through a stem of two stride-2 3 × 3 convolutions to H 4 × W 4 × C . Four stages then halve resolution and double width ( H 2 i +1 × W 2 i +1 × 2 i − 1 C , i = 1 , . . . , 4 ), with stride-2 convolutions between stages.
In Section III-B, the text states that the stem reduces the input radiograph to , and then states: "Four stages then halve resolution and double width (), with stride-2 convolutions between stages." For (Stage 1), the formula yields a spatial resolution of (which does not halve the stem output resolution) and for (Stage 4) it yields . However, later in Section III-B and Section III-C, Stage 3 and Stage 4 at are stated to have tokens () and tokens (), which agrees with the formula , meaning Stage 1 does not halve resolution relative to the stem output. Furthermore, Figure 1 shows the downsample blocks placed at the end of Stages 1, 2, and 3 (so Stage 1 operates at ), rather than between stages prior to doubling width.
2. Inconsistent parameter dimensions for B_t and C_t in Eq. (5) — Editorial
In Section III-C, the text defines the selective scan projections and recurrence as: " (), and . Discretizing the diagonal and via (1) gives and a single row-major scan over the state : ." Because and (with and ), the Hadamard product requires . However, the zero-order-hold discretization in Eq. (1) applied to , , and requires broadcasting as (or defining ), which is omitted from the definition comparing Eq. (1) and Eq. (5).
3. Low seed count for faithful hidden-state SASF ablation — Major
The faithful Spatial-Mamba operator [21], which applies SASF to the latent states ht before contraction with Ct via the unfused selective_scan_ref recurrence (Row F, 3 seeds), reaches 0.812 ± 0.002 on ChestMNIST (+0.001 vs. Row 9, p = 0.482), 0.749 ± 0.008 on Indiana (−0.001), and 0.795±0.004 on NIH (0.000), but trains 3.8× slower because the dstate = 16 state tensor is materialized in GPU memory.
The comparison between output-space SASF (Row 9, 10 seeds) and faithful hidden-state SASF (Row F) uses only 3 seeds for Row F, which gives low statistical power to detect small accuracy differences on the scale of 0.001–0.003 AUC.
4. Confounded comparison between random-init ablations and pretrained Stage 4 — Major
which we test by ablation. Stages 1–3 load official ImageNet- 1K MambaVision weights [20] and Stage 4 loads ImageNet- 1K Spatial-Mamba weights [21], whose Stage-4 widths match at Small and Base. For Tiny (Spatial-Mamba-T width
In Table VII, default Spatial-MambaVision-T (Row 9) initializes Stage 4 from ridge-projected ImageNet-1K Spatial-Mamba-T weights, whereas topology-changing ablations such as Row 5 (param-matched attention, w=416) and Row B (gated dilated DWConv without SSM) lack matching pretrained checkpoints; comparing them against Row 9 rather than Row 8 (random Stage-4 init, 0.809 AUC) partially confounds operator topology with Stage-4 pretraining.
5. Claimed improvements on localized findings are not statistically significant — Minor
Replacing Stage 4 does not degrade localized nodular or pleural findings (Nodule +0.008, Pleural Thickening +0.006, Mass +0.004), whereas losses concentrate on diffuse parenchymal and fibrotic opacities (Pneumonia −0.015, Fibrosis −0.012, Infiltration −0.010).
The statement that replacing Stage 4 does not degrade localized nodular or pleural findings relies on point estimates (+0.008 for Nodule, +0.006 for Pleural Thickening, +0.004 for Mass) whose 95% confidence intervals for Pleural Thickening (±0.008) and Mass (±0.007) span zero and reach down to -0.002 and -0.003, respectively, without formal per-class equivalence testing.
6. Absence of difference at 80 epochs inferred from p = 0.096 — Minor
ImageNet-1K images. Relative to zero-padding and random initialization, ridge mapping lowers feature reconstruction error ( 0 . 064 vs. 0 . 218 ), improves 1-epoch linear-probe Macro-AUC on ChestMNIST ( 0 . 584 vs. 0 . 538 zero-padding and 0 . 512 random), and speeds Epoch-5 convergence ( 0 . 771 ± 0 . 004 vs. 0 . 719 ± 0 . 006 random), but reaches a statistically indistinguishable final test AUC after 80 epochs ( 0 . 811 ± 0 . 002 vs. 0 . 809
Concluding that ridge-projected initialization and random Stage-4 initialization reach a statistically indistinguishable final test Macro-AUC relies on a non-significant difference test (Δ = -0.002 on ChestMNIST, -0.003 on Indiana, -0.002 on NIH; p = 0.096) rather than a formal TOST equivalence test or reporting the two-level bootstrap confidence interval.
7. Per-pathology specificity thresholds appear calibrated on the test set — Minor
Because deployment calibrates per-pathology thresholds to a target false-positive rate, we also report sensitivity at 90% specificity (Sens@90%Spec).
While checkpoints are selected by validation Macro-AUC, the text does not specify whether the per-pathology decision thresholds for the 90% specificity operating point in Table V were calibrated on the validation split and applied to the test split, or read directly off the test ROC curves, which could introduce mild optimistic bias for rarer classes.
8. Symmetric knowledge distillation evaluated only at Tiny scale — Major
Symmetric KD control (Tiny): MambaVision-T + KD
The symmetric knowledge distillation control is only reported for the Tiny scale in Table III, leaving untested whether distilling the unreplaced Small and Base baselines from MambaVision-B (or an ensemble/larger teacher) produces the same 0.002–0.005 symmetric gap across all scales.
9. Distilled Spatial-MambaVision-B vs. MambaVision-S Pareto comparison omitted — Major
Spatial-MambaVision-T (20.05M) and -S (32.14M) occupy favorable points on the accuracy–parameter curve, but undistilled Spatial-MambaVision-B (77.63M, 14.20 GFLOPs) is Pareto-dominated by the unreplaced MambaVision-S (49.38M, 7.50 GFLOPs), which uses 36.4% fewer parameters and 47.2% fewer GFLOPs while scoring 0.002–0.003 higher on all three datasets (0.820 vs. 0.818 on ChestMNIST, 0.761 vs. 0.758 on Indiana, 0.805 vs. 0.803 on NIH), a consequence of the wider Base Stage-4 FFN/SSM ratios.
The Pareto-dominance argument against Base-scale replacement compares undistilled Spatial-MambaVision-B (0.818 / 0.758 / 0.803) with undistilled MambaVision-S (0.820 / 0.761 / 0.805), omitting that distilled Spatial-MambaVision-B+KD (Table III: ΔAUC of 0.002 vs. 0.823/0.764/0.809, i.e., ~0.821 / 0.762 / 0.807) slightly exceeds undistilled MambaVision-S, which would require comparing against distilled MambaVision-S+KD to confirm strict dominance under KD.
XSci (AI review)
Summary
The authors ask what MambaVision's parameter-heavy fourth stage contributes to multi-label chest radiograph classification. They replace all Stage-4 hybrid blocks with lighter single-scan state-space blocks adapted from Spatial-Mamba, applying the dilated depthwise fusion (SASF) to the scan output rather than to the latent states, and keep Stages 1-3 with their ImageNet weights. Tiny, Small and Base variants are evaluated over nine dataset-scale cells drawn from ChestMNIST, a 7,121-image NIH high-resolution subset and Indiana Open-i, with ablations against pruning, reduced-MLP and convolutional controls. Replacement cuts parameters by 19.7%-35.7% and raises FP16 throughput by 10.7%-19.3% at a cost of 0.003-0.006 Macro-AUC; distillation narrows the gap to 0.001-0.002, but distilling the baseline as well leaves 0.002-0.005, and at Base scale the unreplaced Small model is both smaller and more accurate.
Contribution and Significance
The contribution is an empirical characterisation rather than a new architecture: a quantified exchange rate between backbone size and diagnostic discrimination for a widely used hybrid backbone. Sections IV-C and IV-E establish the part that will outlast the paper, namely that Stage 4 holds 58.1%-64.9% of parameters but only 19.8% of GFLOPs, and that at 512 x 512 its quadratic attention contributes 0.332 of 24.18 GFLOPs (1.4%), so the saving is parameter-driven and not complexity-driven. For a J-BHI readership building screening tools, Tables II, III and V together are a usable deployment data point.
What is genuinely new relative to the closest prior work is narrow. The backbone is MambaVision [20] unchanged in Stages 1-3; the replacement block is Spatial-Mamba [21] taken essentially as published. The one deviation, output-space rather than hidden-state SASF, is shown by the authors' own Row F to be indistinguishable from the faithful operator (0.812 vs 0.811, p = 0.482), so it is an implementation convenience, not a modelling advance. Nothing in SASSM is specific to thoracic anatomy, and Spatial-MambaVision is less accurate than its own baseline in all nine cells of Table III. The paper's value rests on the measurement and on the candour of the reporting, not on the model.
Strengths
- The controls argue against the authors' own construction and are reported anyway: the symmetric distillation control (Table VII, Row 1K) raises MambaVision-T to 0.817 and leaves a 0.002-0.005 gap, and Section IV-D reports that Spatial-MambaVision-B (77.63M) is Pareto-dominated by MambaVision-S (49.38M, 0.820 vs 0.818).
- The two-resolution FLOP decomposition (Sections IV-C and IV-E) separates parameter cost from attention cost and corrects a common assumption about where efficiency gains in hybrid backbones come from.
- Row F of Table VII is a reusable engineering result: output-space SASF matches the hidden-state operator of [21] while staying compatible with the fused scan kernel, which trains 3.8x faster.
- The statistical treatment is above the norm for this literature: 10 seeds, two-level bootstrap over seeds and radiographs, a pre-stated +/-0.005 TOST margin, Holm adjustment across the nine cells, and a per-class breakdown (Table V) showing that losses concentrate on diffuse opacities (Pneumonia -0.015, Fibrosis -0.012, Infiltration -0.010) while nodular and pleural findings improve (Nodule +0.008). Every number I checked, including the Table V class means and the 512 x 512 scaling arithmetic, is internally consistent.
Recommendation
Major Revision for IEEE Journal of Biomedical and Health Informatics. The characterisation is careful, the controls are honest, and the result is usable by readers deploying chest radiograph classifiers, which clears the venue's bar for a measurement paper. What stands in the way is that the headline 0.003-0.006 figure comes from a test split against which the proposed configuration appears to have been selected, that the distillation teacher is unspecified and has a concrete leakage route on the NIH subset, and that "where should the budget be cut" is answered only inside Stage 4. All three are addressable within the present approach.
Major Concerns
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Design and distillation hyperparameters appear to be selected on the reported test split (Section IV-F, Table VII; Section IV-B). Table VII reports "ChestMNIST AUC" values that match the test-set numbers of Tables III and IV exactly (Row 1 = 0.815, Row 9 = 0.811, Row 10 = 0.814), so the ablation table is the test split, and no validation-set ablation is given anywhere. Section IV-F then states that over alpha in {0.25, 0.5, 0.75} and tau in {1, 2, 4} the distilled AUC "stays within 0.812-0.814, peaking at the default alpha = 0.5, tau = 2": the default is the maximum of a sweep on the reported metric. The dilation schedule, FFN ratio and initialisation were likewise chosen among configurations whose test scores appear in Table VII, whereas Section IV-B says baselines "received the same search budget over learning rate and weight decay" only. The differences at stake (0.003-0.006) are the size of the spread across Rows C1, C2, D, E and F (0.810-0.812), so the asymmetry can move the central number. Please state which split supported every selection decision and re-run the selection on validation Macro-AUC.
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The same-budget controls are all internal to Stage 4 (Table VII, Rows A, 2, P, 3 and 5; Section IV-D). Row P prunes "MambaVision-T's Stage-4 mixer and MLP channels" and the others reduce Stage-4 depth, width or MLP ratio. These establish that SASSM is the best way to shrink Stage 4, but H2 and the recommendation that "replacement therefore suits only the 20M-35M hybrid regime" require the stronger statement that Stage 4 is the right place to shrink. Section I reports that Stage 3 holds 29.0% of MambaVision-T parameters, and the authors' own Base-scale finding shows that reducing overall scale can dominate Stage-4 replacement. The Tiny analogue is missing: a whole-backbone Taylor-importance pruning of MambaVision-T to roughly 20M, which reuses the machinery of Row P and costs one fine-tuning run. If that control also lands below 0.811 the claim is considerably stronger; if it does not, the conclusion needs revising.
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The distillation teacher's training cohort is never stated, and on the NIH subset it may have seen the test radiographs (Section III-D; Section IV-A). The manuscript says only that KD uses "a fine-tuned MambaVision-B teacher" and that "the common teacher lets us apply the identical recipe" to both students, without saying on which cohort that teacher was fine-tuned. This matters because the authors themselves report that 2,514 of the 3,592 NIH-subset test radiographs (70.0%) lie in the ChestMNIST training split. If a single ChestMNIST-fine-tuned teacher supplied logits for the NIH-subset students, those students were supervised by a model trained on 70% of their own test set, and the NIH KD rows of Table III, including the equivalence result at NIH-Tiny (p_TOST_KD = 0.009), are optimistic. Please state the teacher's fine-tuning data for each cell, and if a shared teacher was used across cohorts, repeat the NIH-subset and Indiana KD runs with a teacher fine-tuned on the corresponding training split only.
Minor Comments
- TOST is computed across seed means whose SDs the authors say "understate full variance" (Section IV-B); report equivalence bounds from the two-level bootstrap instead, which matters for the borderline passes at ChestMNIST-Small (p_TOST = 0.047, CI [0.001, 0.005]) and NIH-Small at 512 x 512 (p_TOST = 0.039, CI [-0.001, 0.005]).
- State which split supplied the per-pathology thresholds behind Sens@90%Spec in Table V; if they were set on the test set, the operating-point numbers are optimistic for both models.
- CheXpert [3] and MIMIC-CXR [23] are cited but unused, so the 0.003-0.006 exchange rate rests on two NIH-derived cells with 70.0% overlap plus one 764-study Indiana cell in which nothing is established; one disjoint external cohort is needed before the figure is offered as a general quantity.
- The Limitations concede that "profiling used PyTorch without TensorRT", but since the throughput gain is the entire benefit on offer, please add torch.compile numbers, as compiled runtimes optimise fused attention heavily while custom selective-scan kernels often lag.
- The anatomical motivation in Section III-C, that "row-major scanning separates vertically and diagonally adjacent lung regions", is asserted rather than tested, and Rows 7, C1 and C2 show the schedule barely matters once non-uniform.
- The 8.9% Indiana figure is presented as a bound on cross-split patient overlap, but it counts only test reports referencing a prior examination, so same-patient pairs in which neither report mentions a prior are not covered.
- Add MambaOut (W. Yu and X. Wang, "MambaOut: Do We Really Need Mamba for Vision?", Proc. IEEE/CVF CVPR, 2025, pp. 4484-4496) to Section II and relate it to Row B, which is essentially its gated-CNN-without-scan block.
- Making DeLong tests and prediction logs "available from the corresponding author on reasonable request" (Section IV-B) is below what readers need to reuse this characterisation; please deposit code, logs and the profiling script.
- In Table III the column headed "Ours+KD" contains differences (0.001-0.002) rather than AUCs; give the absolute values or relabel the column.
- The title "Trading Parameters for Accuracy" reads as spending parameters to buy accuracy, which is the opposite of what the paper reports.
- "mg/s" should be "img/s" in Section IV-D (twice) and Section IV-E.
- Reference [18] is printed before [17] in the reference list.