Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

This study compared six behavior‑classification models using neck‑mounted six‑axis IMU data collected from 19 Korean black goats, with evaluations conducted under both window‑level and subject‑level validation protocols. The key findings demonstrate that a 24‑dimensional learned representation achieves performance comparable to that of a 250‑dimensional hand‑crafted feature set; notably, two structurally distinct encoders yielded equivalent classification accuracy. It was the training objective, rather than network architecture, that exerted the dominant influence on representation quality.

Although the paper contains sufficient experimental data, I argue that the conclusion that a 24‑dimensional learned representation achieves classification accuracy comparable to the 250‑dimensional hand‑crafted feature set is supported merely by this specific pair of comparative experiments, which makes the methodological design rather one‑sided. The authors should validate additional alternative model configurations to verify the uniqueness of this conclusion. The paper can be considered sound only after the uniqueness of the conclusion is demonstrated.

In addition, the contents of Figure 3, Figure 4 and Figure 5 are not sufficiently clear, and these figures need to be redrawn.

Author Response

Response to Reviewer 1 Comments

Manuscript ID: sensors-4553923

Title: Handcrafted Features versus Learned Representations for IMU-Based Goat Behavior Classification: Accuracy, Validation Design, and Computational Cost

1. Summary

Thank you very much for taking the time to review this manuscript. Please find the detailed responses below and the corresponding revisions marked in blue in the resubmitted manuscript. Before the point-by-point responses, we report three corrections that we identified during the revision; none of them changes the conclusions.

2. Corrections identified by the authors

First, while re-examining the data pipeline for this revision, we found that the integer codes of the two focal classes had been interchanged in the curated dataset relative to the class names used in the manuscript: the windows reported as Rumination were in fact eating, and vice versa. We confirmed this against the original annotation files and their metadata, by byte-level matching of raw signal windows between the manually annotated set and the curated dataset, and by the motion signature of each class (gyroscope magnitude about five times higher in the windows now labeled Eating than in those labeled Rumination). Because Macro F1 is invariant to a permutation of class names, no Macro F1 value, model ranking, contrast, sampling-rate or latency result changes. We have corrected Table 1, the per-class columns of Tables 5 and 6 and of Table S2, Figure 6 and every sentence that names a class, and have rewritten the two interpretations that depended on the class names: the ordering of class difficulty and the class-dependent deficit of Model F:

“Eating in a pen-fed system involves large, sustained head and neck movements toward the feed trough, which produce a high-amplitude, readily separable signature at the collar. Rumination is a low-motion state in which the only consistent signal is the small rhythmic jaw movement of chewing [37]; against this quiet background it shares much of its signal envelope with resting and other inactive states.” (Section 4.1, page 20, lines 692–697)

“The deficit was strongly class-dependent, smallest for Eating (0.040 under LOSO), intermediate for Rumination (0.123), and largest for Other (0.218), consistent with the class-difficulty ordering. One plausible explanation is that the mean-squared reconstruction objective is dominated by high-amplitude signal components. The large head movements of eating contribute substantially to reconstruction error if omitted, so a representation optimized for reconstruction has reason to retain them. Separating rumination from the other low-motion states, by contrast, depends on small-amplitude chewing pulses [37] that contribute little to reconstruction fidelity and are therefore not prioritized by the objective.” (Section 4.2, page 20, lines 715–723)

Second, per-subject Macro F1 under LOSO is now averaged over the classes present in each subject’s held-out partition. Seven of the 15 LOSO subjects contributed no Other windows (Table S4), and the previous computation had assigned them an F1 of zero for that class. The per-subject values in Table 4 and the statistics derived from them, such as the ratio of between-subject variability to the spread among models (now roughly five-fold rather than 4.5-fold), have been recomputed; aggregate Macro F1 is unaffected. We also found that the largest difference in aggregate Macro F1 between the re-executed confusion matrices of Figure 6 and Table 5 is 0.003, not 0.005 as previously stated, so run-to-run variation is now described as more than half, rather than larger than, the 0.0048 difference between Models A and B:

“…the mean ± SD of per-subject Macro F1 (n = 15), where each subject’s Macro F1 is averaged over the classes present in its held-out partition.” (Section 2.7, page 12, lines 424–426)

“The full range of per-subject mean Macro F1 across Models A–E was 0.025, smaller than the between-subject standard deviation by a factor of approximately 5.” (Section 3.1, page 14, lines 527–529)

“…per-class F1 derived from them differs from Table 5 by at most 0.006, and aggregate Macro F1 by at most 0.003, reflecting non-deterministic GPU execution.” (Section 3.2.1, pages 14–15, lines 548–550)

Third, in preparing the new Figure 1, which now shows the sensor axes relative to the animal’s body, we found that the axis assignment in the original Section 2.1 was incorrect. The text stated that gravity was registered on the −Y axis and took Y as the dorsoventral axis; gravity is in fact carried by the X axis, which runs along the collar strap. No result depends on this description, because all models received the raw axis-native signals. The corrected description reads:

“The X axis runs along the collar strap (positive ventrally), the Y axis is normal to the neck surface (positive outward), and the Z axis runs along the neck (positive cranially).” (Section 2.1, page 4, lines 136–137)

We apologize for these errors. We have also re-checked every citation against its source and revised the wording where it did not match the cited study; these changes are marked in blue as well.

3. Point-by-point response to Comments and Suggestions for Authors

Comments 1: The conclusion that a 24-dimensional learned representation achieves classification accuracy comparable to the 250-dimensional handcrafted feature set is supported merely by this specific pair of comparative experiments, which makes the methodological design rather one-sided. The authors should validate additional alternative model configurations to verify the uniqueness of this conclusion.

Response 1: Thank you for this comment. The parity was in fact reached twice, by two feature extractors of different architecture (the attention network of Model B and the attention-free multi-scale CNN of Model E), each compared with the same handcrafted baseline (Table 7, contrasts A → B and A → E). Because the design already varies the extractor, the classifier and the training objective one at a time on identical data, we have not added further architectures. Instead, the comparison is now tested with a linear mixed model, and a pilot comparison of bottleneck dimensions is reported next to the statement that 24 dimensions are sufficient rather than optimal:

“A linear mixed model was fitted with model (A–F) as a fixed effect and subject as a random intercept, using R version 4.6.1 [31] and the lme4 package [32].” (new Section 2.11, page 13, lines 491–492)

“The mixed model indicated a significant overall effect of model (F(5, 70) = 13.1, p < 0.001), but no pairwise contrast among Models A, B, D, and E reached significance (Tukey-adjusted p ≥ 0.97).” (Section 3.1, page 13, lines 503–505)

“A pilot comparison of d = 2, 4, and 8 (24, 48, and 96 features), run on an earlier version of the dataset with a different validation protocol and a KNN classifier, gave Macro F1 of 0.772, 0.777, and 0.779; these values are not directly comparable to the main experiments. The results below therefore show that 24 dimensions suffice for this task, not that 24 is optimal.” (Section 2.4.3, page 8, lines 294–298)

Comments 2: In addition, the contents of Figure 3, Figure 4 and Figure 5 are not sufficiently clear, and these figures need to be redrawn.

Response 2: Thank you. We agree. Figures 3, 4 and 5 have been redrawn at 600 dpi with larger fonts, and their content has been clarified (pages 7, 10 and 12). Figure 3 now also shows the attention configuration (four heads, d_k = 1), the token dimension (d_model = 4), the output Z′ and both downstream classifiers (LightGBM for Model B, KNN for Model C). In Figure 4 the decoder of Model F is drawn as a training-only branch, and its correlation features are shown. In Figure 5 subject-level LOSO, now the primary validation scheme, is panel (a), and the held-out partition is labeled as such; the caption has been revised accordingly:

“Figure 5. The two validation schemes. (a) Subject-level leave-one-subject-out over the 15 subjects with at least 50 windows per target class, the primary scheme; (b) Stratified 5-fold cross-validation with window-level shuffling (seed = 42), interpreted as an upper bound of representational capacity.” (Figure 5, page 12, lines 429–431)

For consistency, Figures 2 and 6–9 have also been redrawn at 600 dpi.

We hope that the revised manuscript addresses your concerns, and we thank you again for your time and helpful comments.

Sincerely,

Na-Yeon Kim, on behalf of all authors

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

This manuscript investigates an IMU-based automated behaviour-recognition framework for distinguishing rumination and eating activities in livestock, with the stated objective of providing a compact sensing and machine-learning solution for continuous behavioural monitoring. The authors develop a two-stage processing pipeline in which a proprietary binary deep-learning model initially separates the target behaviours from other behavioural states, followed by a KNN-based classification stage using handcrafted features to discriminate between rumination and eating. This topic is highly relevant and aligns well with the scope of the Sensors Journal, however, several concerns regarding the manuscript need to be addressed as follows:

1 The proposed two-stage automatic labelling procedure first employs a proprietary binary deep-learning model to distinguish rumination and eating from other behavioural states, followed by a KNN classifier based on handcrafted features to discriminate between the two target behaviours. Importantly, both stages rely on the same IMU-derived signals that are subsequently used for model development. This configuration raises a potential risk of label leakage or circularity, particularly because the classification process is not fully independent of the input representation used by the evaluated models. Although the authors report 99.3% agreement with synchronized video annotations on a stratified sample of 600 windows, the validation procedure appears to retain only windows for which the five nearest neighbours in the KNN classifier unanimously support the assigned label. Consequently, the evaluated subset may be enriched for samples that are inherently well separated within the manufacturer's feature space, potentially inflating the apparent reliability of the automatically generated labels. This issue is especially relevant for Model A, whose handcrafted features may substantially overlap with those used during the KNN-based labeling stage; however, the potential effect extends to the other models because all are trained using labels generated through the same procedure. The authors should therefore clarify the independence between label generation, feature extraction, model training, and label validation, and provide an evaluation on an independently annotated dataset in which human experts continuously annotate the complete sequence rather than only preselected high-confidence windows.

2 The finding that a 24-dimensional learned representation matches the 250-dimensional handcrafted baseline is presented as a central result; however, the bottleneck dimension was fixed a priori at 24 without any systematic exploration. As the authors note in Section 2.4.3, the choice of d=2 was the most aggressive reduction available in the architectural family and was not tuned. The results therefore demonstrate that 24 dimensions are sufficient, not that they are optimal or that the intrinsic dimensionality of the task is 24. The parity achieved by two structurally unrelated architectures (Model B and Model E) is indeed compelling evidence that the result is not an artifact of a particular architecture, but the sufficiency interpretation should be stated with appropriate caution. The authors would be well advised to include a sensitivity analysis across bottleneck dimensions, or at minimum to frame the result more carefully in terms of sufficiency rather than optimality.

3 The gap between 5-fold CV and LOSO ranges from 0.044 to 0.095, and between-subject variability substantially exceeds between-model differences. The authors conclude that accuracy is not a usable criterion for selecting among the leading models and that selection should rest on operational properties. This conclusion is reasonable given the paired tests in which no pairwise comparison among Models A, B, and D reached significance (p = 0.151, 0.277, and 0.720). However, the statistical power of these tests should be considered. With n=15 subjects, the ability to detect a difference of the magnitude observed here (0.005-0.006) is limited. The manuscript would benefit from a more explicit discussion of the effect sizes and confidence intervals around the model comparisons, rather than relying solely on p-values.

4 Features that depend on frequency content above the Nyquist limit are set to zero, and the same 250 feature indices selected at 25 Hz are reused at all lower rates. This means Model A's performance at reduced sampling rates is a conservative estimate of what the handcrafted pipeline could achieve if feature selection were re-executed at each rate. The authors acknowledge this limitation, but the acknowledgment should be accompanied by a meaningful interpretation of the results. The front-loaded gains below 15 Hz are robust to this implementation choice, since both the handcrafted and learned models show diminishing returns above 10-15 Hz. However, the comparisons at individual rates, particularly the widening gap between Models A and B at lower sampling rates under 5-fold CV, should be interpreted with caution. It would be desirable to re-run the handcrafted feature selection at each sampling rate to establish whether the observed gap is an artifact of the zero-filling and fixed feature indices or a genuine advantage of learned representations at low temporal resolution.

5 The pairwise Wilcoxon tests reported in Section 3.1 compare Models A, B, and D, but the manuscript does not clearly state whether these tests were planned or post-hoc, nor whether adjustments for multiple comparisons were applied. Given the number of potentials pairwise comparisons across six models and two validation schemes, the absence of such adjustments could inflate the type I error rate. The authors should clarify their statistical testing strategy and consider reporting effect sizes alongside p-values.

6 Model A's handcrafted feature extraction is implemented in Python/NumPy without compiled optimization, whereas Models B and D execute through PyTorch operators backed by optimized compiled kernels. The reported speedups therefore reflect the implementation choices as much as the inherent computational cost of the two paradigms. The authors acknowledge this limitation in Section 2.9, noting that latency measurements serve as a proxy for edge deployment and that absolute latency on production hardware will differ. The framing is appropriate, but the manuscript would be strengthened by a more explicit discussion of the engineering considerations that determine whether a PyTorch-based inference pipeline can be deployed on an ARM Cortex-M-class microcontroller, or whether the comparison is primarily illustrative of the relative scaling properties.

7 The abstract and conclusions would benefit from more precise language regarding the claims of generalizability. The abstract states that "a 24-dimensional learned representation matched a 250-dimensional handcrafted feature set," which is supported by the results, but the subsequent implication that "feature dimensionality can be cut by 90% and sampling rate reduced to 10-15 Hz with little accuracy loss" should be qualified by the dataset characteristics. The manuscript demonstrates this on a dataset of sustained, unambiguous behavioural episodes from 19 animals at a single site over nine days. The conclusions should more explicitly acknowledge that the recommended operating points apply to similar conditions and that generalization to other breeds, housing systems, sensor placements, and behavioural distributions remains to be established.

8 The references are generally appropriate and up-to-date, including several 2024-2025 publications. However, the manuscript would benefit from a more critical synthesis of the recent literature on validation design in animal behaviour classification. The work of Wang et al. (2025) and Wilson et al. (2025) is cited, but a more extended discussion of how the present findings relate to these studies would strengthen the positioning of the work. The authors could also consider citing recent work on self-supervised learning for IMU-based patterns recognition beyond the reconstruction objectives tested here, to contextualize their finding that reconstruction is suboptimal for this task.

9 The confusion matrices in Figure 6 are row-normalized, which is appropriate for comparing recall across classes, but the text in Section 3.2.2 also discusses precision implicitly when interpreting the Other-Eating confusion. A column-normalized version or a combined presentation showing both recall and precision would help readers understand the direction of misclassifications more completely. The inference latency plot in Figure 8 uses a log scale, which is appropriate given the range of values, but the legend could be more informative about which measurements are CPU versus GPU.

10 The mathematical notation in Sections 2.4.3-2.4.5 is generally correct, but the explanation could be clearer in places.

Comments on the Quality of English Language

The English could be improved to more clearly express the research. Several passages contain redundant expressions or unnecessary modifiers that could be streamlined without loss of meaning. The manuscript frequently relies on nominalized verbs and passive constructions where active phrasing would be more direct and concise. Some technical terms are used inconsistently or in ways that could confuse readers. Several sentences contain minor grammatical issues or awkward phrasing that could be corrected with modest revision. Some sentences are unnecessarily long and complex, making them difficult to follow. Some sentences contain missing or inconsistent articles.

Author Response

Response to Reviewer 2 Comments

Manuscript ID: sensors-4553923

Title: Handcrafted Features versus Learned Representations for IMU-Based Goat Behavior Classification: Accuracy, Validation Design, and Computational Cost

1. Summary

Thank you very much for taking the time to review this manuscript. Please find the detailed responses below and the corresponding revisions marked in blue in the resubmitted manuscript. Each response states briefly what was changed and where, followed by the revised text; page and line numbers refer to the revised manuscript. Before the point-by-point responses, we report three corrections that we identified during the revision (Section 2); none of them changes the conclusions.

2. Corrections identified by the authors

“…the mean ± SD of per-subject Macro F1 (n = 15), where each subject’s Macro F1 is averaged over the classes present in its held-out partition.” (Section 2.7, page 12, lines 424–426)

We apologize for these errors. We have also re-checked every citation against its source and revised the wording where it did not match the cited study; these changes are marked in blue as well.

3. Point-by-point response to Comments and Suggestions for Authors

Comments 1: The proposed two-stage automatic labelling procedure first employs a proprietary binary deep-learning model to distinguish rumination and eating from other behavioural states, followed by a KNN classifier based on handcrafted features to discriminate between the two target behaviours. Importantly, both stages rely on the same IMU-derived signals that are subsequently used for model development. This configuration raises a potential risk of label leakage or circularity, particularly because the classification process is not fully independent of the input representation used by the evaluated models. Although the authors report 99.3% agreement with synchronized video annotations on a stratified sample of 600 windows, the validation procedure appears to retain only windows for which the five nearest neighbours in the KNN classifier unanimously support the assigned label. Consequently, the evaluated subset may be enriched for samples that are inherently well separated within the manufacturer's feature space, potentially inflating the apparent reliability of the automatically generated labels. This issue is especially relevant for Model A, whose handcrafted features may substantially overlap with those used during the KNN-based labeling stage; however, the potential effect extends to the other models because all are trained using labels generated through the same procedure. The authors should therefore clarify the independence between label generation, feature extraction, model training, and label validation, and provide an evaluation on an independently annotated dataset in which human experts continuously annotate the complete sequence rather than only preselected high-confidence windows.

Response 1: Thank you. We agree that label independence is the main limitation of the study and have addressed it in four ways.

(a) Section 2.2 now describes each stage of the labeler with the number of windows passing it, states that the architecture of the manufacturer’s binary screening model is not disclosed, and gives the share of final windows from manual annotation and from the automatic labeler:

“A two-stage automatic labeler was then applied to the full recordings (1,416,961 windows over 164 animal-days). … The binary screening model was developed by the sensor manufacturer, and its architecture is not disclosed here. Because the KNN stage uses the same handcrafted feature family as Model A, the labels are not fully independent of Model A’s input representation. Of the 132,887 windows in the final dataset, 78,320 (58.9%), including Other windows, originated directly from manual annotation and 54,567 (41.1%) from the automatic labeler.” (Section 2.2, pages 4–5, lines 158–172)

(b) Because the labeler’s KNN stage uses the same handcrafted feature family as Model A, the circularity it introduces is most relevant to Model A and, if anything, works against the learned representations that matched it. It does not confound the B-versus-C contrast, because the KNN of Model C operates on the learned representation. The screening stage, whose architecture is not disclosed, is characterized only empirically:

“About 41% of the final windows were assigned by the automatic labeler, whose KNN stage uses the same handcrafted feature family as Model A; this potential circularity is therefore most relevant to Model A, and if anything biases the comparison against the learned representations that matched it.” (Section 4.5, page 23, lines 841–844)

“This contrast is not confounded by the labeler, whose KNN stage operated on handcrafted features rather than on the learned representation.” (Section 4.3, page 21, lines 757–758)

“The binary screening stage of the labeler was supplied by the sensor manufacturer and its architecture is not disclosed, so the reliability of that stage is characterized empirically, by agreement with synchronized video, rather than by specification.” (Section 4.5, page 23, lines 877–880)

(c) The 600-window video check is now reported with Wilson 95% confidence intervals:

“Agreement between the assigned labels and the human video assessment was 99.3% overall (596/600; Wilson 95% CI 98.3–99.7%): Rumination 98.5% (95.7–99.5%), Eating 99.5% (97.2–99.9%), and Other 100.0% (98.1–100.0%).” (Section 2.2, page 5, lines 175–177)

As before, Section 4.5 (paragraph 1) notes that this check does not remove the selection bias introduced by the unanimity filter.

(d) Continuous annotation of the complete recording was not feasible within this revision; it remains the first direction for future work (Section 4.5, paragraph 6). The Abstract and the objectives now state how the labels were generated:

“…with labels from a semi-automatic procedure verified against synchronized video.” (Abstract, page 1, lines 32–33)

“Ground-truth labels were produced by a semi-automatic procedure combining manual video annotation with automatic labeling, verified on a stratified sample against synchronized video.” (Introduction, page 3, lines 100–102)

Comments 2: The finding that a 24-dimensional learned representation matches the 250-dimensional handcrafted baseline is presented as a central result; however, the bottleneck dimension was fixed a priori at 24 without any systematic exploration. As the authors note in Section 2.4.3, the choice of d=2 was the most aggressive reduction available in the architectural family and was not tuned. The results therefore demonstrate that 24 dimensions are sufficient, not that they are optimal or that the intrinsic dimensionality of the task is 24. The parity achieved by two structurally unrelated architectures (Model B and Model E) is indeed compelling evidence that the result is not an artifact of a particular architecture, but the sufficiency interpretation should be stated with appropriate caution. The authors would be well advised to include a sensitivity analysis across bottleneck dimensions, or at minimum to frame the result more carefully in terms of sufficiency rather than optimality.

Response 2: Thank you. The result was already framed as sufficiency in Section 2.4.3 and the Limitations; we have kept this framing and now also report a pilot comparison of d = 2, 4 and 8 with its conditions stated. A full sweep under the main protocol was not feasible within this revision:

“The bottleneck dimension was fixed at 24 in the main experiments, and the pilot comparison of 24, 48, and 96 dimensions (Section 2.4.3) was run under non-comparable conditions, so the results establish the sufficiency of 24 dimensions, not the intrinsic dimensionality of the task.” (Section 4.5, page 23, lines 874–877)

Comments 3: The gap between 5-fold CV and LOSO ranges from 0.044 to 0.095, and between-subject variability substantially exceeds between-model differences. The authors conclude that accuracy is not a usable criterion for selecting among the leading models and that selection should rest on operational properties. This conclusion is reasonable given the paired tests in which no pairwise comparison among Models A, B, and D reached significance (p = 0.151, 0.277, and 0.720). However, the statistical power of these tests should be considered. With n=15 subjects, the ability to detect a difference of the magnitude observed here (0.005-0.006) is limited. The manuscript would benefit from a more explicit discussion of the effect sizes and confidence intervals around the model comparisons, rather than relying solely on p-values.

Response 3: Thank you. We agree. The Wilcoxon tests have been replaced by a linear mixed model with subject as a random intercept, and Section 3.1 now reports the estimated differences with Tukey-adjusted 95% confidence intervals and effect sizes:

“A linear mixed model was fitted with model (A–F) as a fixed effect and subject as a random intercept, using R version 4.6.1 [31] and the lme4 package [32]. Estimated marginal means and Tukey-adjusted pairwise contrasts with 95% confidence intervals were obtained with the emmeans package [33], and paired Cohen’s d_z is reported as the effect size for the contrasts discussed in the text.” (new Section 2.11, page 13, lines 491–495)

“Estimated differences among these four models were at most 0.008, and every Tukey-adjusted 95% confidence interval included zero (A versus B, 0.006 [−0.027, 0.040], d_z = 0.45; A versus D, 0.006 [−0.027, 0.040], d_z = 0.19; B versus D, 0.000 [−0.033, 0.033], d_z = 0.00).” (Section 3.1, page 13, lines 505–508)

The Discussion now interprets the differences against these intervals, against run-to-run variation and against the two summary statistics; the last sentence below replaces the earlier statement that Model D’s aggregate advantage rests on subjects contributing more windows:

“Under LOSO the aggregate difference was 0.005, and the per-subject difference of 0.006 had a Tukey-adjusted 95% confidence interval of −0.027 to 0.040; both are small next to the between-subject variability.” (Section 4.1, page 19, lines 664–666)

“Re-execution under identical seeds shifted the aggregate Macro F1 of Models A, B, and D by up to 0.003 (Section 3.2.1), more than half the 0.0048 difference between Models A and B under LOSO; the smallest between-model gaps are therefore of the same order as run-to-run variation alone. The ranking by aggregate Macro F1 (Model D first) and by per-subject mean (Model A first) differed, but by margins well within these confidence intervals.” (Section 4.3, page 21, lines 767–772)

We did not compute post hoc power, because the intervals already show that differences larger than about 0.03–0.04 are excluded, whereas differences of the observed size are not. The per-subject statistic used in these analyses has also been corrected (see Section 2 above).

Comments 4: Features that depend on frequency content above the Nyquist limit are set to zero, and the same 250 feature indices selected at 25 Hz are reused at all lower rates. This means Model A's performance at reduced sampling rates is a conservative estimate of what the handcrafted pipeline could achieve if feature selection were re-executed at each rate. The authors acknowledge this limitation, but the acknowledgment should be accompanied by a meaningful interpretation of the results. The front-loaded gains below 15 Hz are robust to this implementation choice, since both the handcrafted and learned models show diminishing returns above 10-15 Hz. However, the comparisons at individual rates, particularly the widening gap between Models A and B at lower sampling rates under 5-fold CV, should be interpreted with caution. It would be desirable to re-run the handcrafted feature selection at each sampling rate to establish whether the observed gap is an artifact of the zero-filling and fixed feature indices or a genuine advantage of learned representations at low temporal resolution.

Response 4: Thank you for this suggestion. We did not re-run feature selection in this revision. As in the original submission, Model A’s values below 25 Hz are treated as a conservative estimate for this reason (Section 3.4, paragraph 2, and Section 4.5, paragraph 4); Section 3.4 now also states that the low-rate difference between Models A and B favors Model A:

“The Macro F1 difference between Models A and B widened as sampling rate decreased under 5-fold CV, in favor of Model A, from 0.000 at 25 Hz to 0.009 at 5 Hz, but showed no comparable trend under LOSO.” (Section 3.4, page 16, lines 599–601)

Re-selection would therefore be expected to widen this difference rather than reverse it. The cost of reduced sampling was also of similar size in Models B, D and E, which do not use the selected indices, so the 10–15 Hz operating point does not depend on this choice:

“Under LOSO, operating at 15 Hz costs 0.003–0.007 in Macro F1 for a 40% reduction in sampled data volume, and 10 Hz costs 0.009–0.012 for a 60% reduction across Models A, B, D, and E.” (Section 4.4, page 22, lines 827–829)

Comments 5: The pairwise Wilcoxon tests reported in Section 3.1 compare Models A, B, and D, but the manuscript does not clearly state whether these tests were planned or post-hoc, nor whether adjustments for multiple comparisons were applied. Given the number of potentials pairwise comparisons across six models and two validation schemes, the absence of such adjustments could inflate the type I error rate. The authors should clarify their statistical testing strategy and consider reporting effect sizes alongside p-values.

Response 5: Agree. The Wilcoxon tests have been replaced. All 15 pairwise contrasts among the six models are now estimated within one linear mixed model with Tukey adjustment, so no contrast is selected post hoc, and fold-level differences under 5-fold CV are not tested:

“Fold-level differences under 5-fold CV were not tested, because folds are resamples of a single dataset rather than independent experimental units.” (Section 2.11, page 13, lines 495–497)

“Model F was significantly below every other model (differences 0.052–0.078, all p < 0.001); no other contrast reached significance.” (Section 3.1, pages 13–14, lines 509–511)

Comments 6: Model A's handcrafted feature extraction is implemented in Python/NumPy without compiled optimization, whereas Models B and D execute through PyTorch operators backed by optimized compiled kernels. The reported speedups therefore reflect the implementation choices as much as the inherent computational cost of the two paradigms. The authors acknowledge this limitation in Section 2.9, noting that latency measurements serve as a proxy for edge deployment and that absolute latency on production hardware will differ. The framing is appropriate, but the manuscript would be strengthened by a more explicit discussion of the engineering considerations that determine whether a PyTorch-based inference pipeline can be deployed on an ARM Cortex-M-class microcontroller, or whether the comparison is primarily illustrative of the relative scaling properties.

Response 6: Thank you. We agree. Section 4.4 now discusses the path from a PyTorch model to a Cortex-M-class device and the expected memory footprint of each stage, and reports a measured comparison of update cost:

“A PyTorch model cannot execute directly on a Cortex-M-class device; the usual path is export to ONNX followed by conversion to an embedded runtime such as TensorFlow Lite Micro or CMSIS-NN, with 8-bit quantization. At that precision the 21K-parameter extractor of Model B occupies roughly 21 KB and the 32K-parameter network of Model D roughly 32 KB, both within the flash budget of common Cortex-M4/M7 parts. The tree-ensemble stage of Models B and E, by contrast, comprises up to 1,500 trees of 63 leaves and would likely occupy more memory than the extractor itself, so the end-to-end design of Model D is the more natural candidate for on-collar inference, whereas the modular designs suit gateway- or server-side inference where the classifier can be refitted cheaply.” (Section 4.4, page 22, lines 815–824)

“On the same workstation, refitting the LightGBM classifier of Model B on precomputed 24-dimensional features took 4.8 s of CPU time (median of three runs), whereas retraining Model D end-to-end took 368 s (36 epochs to early stopping).” (Section 4.4, page 22, lines 799–801)

In addition, Section 2.9 no longer describes the workstation latencies as a proxy for edge deployment, and the Abstract qualifies the speed-up as holding in this implementation:

“They characterize relative computational cost across models, not latency on embedded hardware such as ARM Cortex-M-class microcontrollers, which would require on-device profiling.” (Section 2.9, page 13, lines 472–474)

“…and the learned pipelines cut inference time by up to 36-fold in this implementation.” (Abstract, page 2, lines 43–44)

The title now refers to computational rather than deployment cost: “Handcrafted Features versus Learned Representations for IMU-Based Goat Behavior Classification: Accuracy, Validation Design, and Computational Cost”.

Comments 7: The abstract and conclusions would benefit from more precise language regarding the claims of generalizability. The abstract states that "a 24-dimensional learned representation matched a 250-dimensional handcrafted feature set," which is supported by the results, but the subsequent implication that "feature dimensionality can be cut by 90% and sampling rate reduced to 10-15 Hz with little accuracy loss" should be qualified by the dataset characteristics. The manuscript demonstrates this on a dataset of sustained, unambiguous behavioural episodes from 19 animals at a single site over nine days. The conclusions should more explicitly acknowledge that the recommended operating points apply to similar conditions and that generalization to other breeds, housing systems, sensor placements, and behavioural distributions remains to be established.

Response 7: Agree. The operating points in the Highlights, the Abstract and the Conclusions are now restricted to the conditions studied:

“Feature dimensionality can be cut by 90% and sampling rate reduced to 10–15 Hz with little accuracy loss under the conditions studied, lowering the communication and computation cost of collar-based behavior monitoring.” (Highlights, page 1, lines 23–25)

“These operating points apply to sustained behavioral episodes under the conditions studied; where accuracy cannot separate models, computational cost should govern the choice.” (Abstract, page 2, lines 44–46)

“These operating points were established for sustained behavioral episodes in housed wethers of a single breed at one site, with labels from a semi-automatic procedure; their transfer to other breeds, housing systems, sensor placements, and natural class prevalence remains to be tested.” (Section 5, page 24, lines 922–925)

Comments 8: The references are generally appropriate and up-to-date, including several 2024-2025 publications. However, the manuscript would benefit from a more critical synthesis of the recent literature on validation design in animal behaviour classification. The work of Wang et al. (2025) and Wilson et al. (2025) is cited, but a more extended discussion of how the present findings relate to these studies would strengthen the positioning of the work. The authors could also consider citing recent work on self-supervised learning for IMU-based patterns recognition beyond the reconstruction objectives tested here, to contextualize their finding that reconstruction is suboptimal for this task.

Response 8: Thank you. We agree. Section 4.3 now compares the gap between the two validation schemes with three cattle studies that reported the same effect, and Rahman et al. (2018) is also introduced in the Introduction. For self-supervised learning, Haresamudram et al. (2022), a systematic assessment of self-supervised objectives for wearable sensors, is now cited in Sections 4.2 and 4.5:

“Inflation of window-level estimates relative to animal-level validation has been reported repeatedly in cattle. Rahman et al. [16] found F-scores decreasing from 0.81–0.93 under stratified cross-validation to 0.15–0.80 under leave-one-animal-out validation on the same dataset, Riaboff et al. [7] likewise reported lower accuracy under cow-level than under sequence-level validation, and Wang et al. [15] reported Macro F1 decreasing from 0.89–0.94 under hold-out validation to 0.64–0.76 under leave-cow-out validation in beef cows fitted with neck-mounted accelerometers sampled at 25 Hz, as in the present study.” (Section 4.3, page 21, lines 737–744)

“Rahman et al. [16] compared within-animal and across-animal partitioning on the same cattle dataset and reported a marked reduction in accuracy under the latter.” (Introduction, page 3, lines 94–96)

“Its performance should be read as a limitation of the specific reconstruction objective tested here, not as evidence against label-free representation learning in general [38-40].” (Section 4.2, page 20, lines 725–727)

“…contrastive and masked-prediction objectives produce discriminative representations without reconstructing every input detail and may reduce annotation requirements in a way a reconstruction objective does not [40,44,45].” (Section 4.5, page 24, lines 898–901)

Comments 9: The confusion matrices in Figure 6 are row-normalized, which is appropriate for comparing recall across classes, but the text in Section 3.2.2 also discusses precision implicitly when interpreting the Other-Eating confusion. A column-normalized version or a combined presentation showing both recall and precision would help readers understand the direction of misclassifications more completely. The inference latency plot in Figure 8 uses a log scale, which is appropriate given the range of values, but the legend could be more informative about which measurements are CPU versus GPU.

Response 9: Agree. Per-class precision (the column-normalized diagonal) and recall for all six models under both validation schemes are now given in the new Table S3, which is cited in Section 3.2.1:

“Per-class F1 under LOSO is given in Table 5, and per-class precision and recall in Table S3.” (Section 3.2.1, page 15, lines 551–552)

Figure 6 has been regenerated with the corrected class labels (see Section 2 above). The legend of Figure 8 now states that solid lines with filled markers are single-thread CPU measurements and dashed lines with open markers are GPU (RTX 3090) measurements.

Comments 10: The mathematical notation in Sections 2.4.3-2.4.5 is generally correct, but the explanation could be clearer in places.

Response 10: Thank you. In Section 2.4.3 we have defined Z′ as the output of the residual layer-normalization step, stated the number and dimension of the attention heads, and defined Models B and C by their classifiers in the opening sentence:

“…followed by a residual connection, dropout, and layer normalization, giving the output Z′.” (Section 2.4.3, page 8, lines 280–281)

“The number of attention heads is set to the largest divisor of d_model not exceeding four; with d_model = 4 this gives four heads of dimension d_k = 1.” (Section 2.4.3, page 8, lines 283–284)

In the Model D equation (Section 2.4.4, page 8, line 311), d has been replaced by d_model, which the text defines as the model dimension of Model D, so that d denotes only the latent dimension of Models B and C.

Comments 11: The English could be improved to more clearly express the research. Several passages contain redundant expressions or unnecessary modifiers that could be streamlined without loss of meaning. The manuscript frequently relies on nominalized verbs and passive constructions where active phrasing would be more direct and concise. Some technical terms are used inconsistently or in ways that could confuse readers. Several sentences contain minor grammatical issues or awkward phrasing that could be corrected with modest revision. Some sentences are unnecessarily long and complex, making them difficult to follow. Some sentences contain missing or inconsistent articles.

Response 11: Thank you. The manuscript has been edited throughout for clarity: long sentences were split, “feature extractor” is used consistently (“encoder” is retained only for the Transformer encoder of Model D and the autoencoder of Model F), and value ranges are written with “to” or an en dash rather than arrows.

We hope that the revised manuscript addresses your concerns, and we thank you again for your time and helpful comments.

Sincerely,

Na-Yeon Kim, on behalf of all authors

Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

The paper is well structured and well written, and the study was well designed and executed. I recommend that the authors address specific comments made in the attached PDF. General comments follow below.

I recommend that the authors expand their literature search to include relevant literature, particularly on beef bulls, cows, and calves, as well as papers on dairy cows. Studies have implemented or tested approaches similar to those described by the authors. Including them and discussing their findings alongside yours would strengthen the paper and properly place the novelty of your study within the field.

The authors used a mixed labelling approach (computer-vision and visual observation) for ground truth. A concern is that the company that provided the sensors also provided the computer-vision software. The authors should address this and discuss whether it could introduce data leakage or compounding uncertainty that affects their results. No inter-rater reliability is presented to assess the consistency of the labelling over time. The authors should also better describe the observations and the composition of the subsampled data.

I suggest the authors emphasize the LOSO results rather than the K-fold results, even though the differences are not as significant. LOSO is a significantly more robust validation method and produces more realistic results for this type of data. I suggest the authors refer to dairy cattle studies (some of which were cited by the author, such as Riaboff et al.) to incorporate statistical tests to compare models. GLM models would be more appropriate for many of the comparisons.

I recommend the authors use computational costs rather than deployment costs. Also, add the programming language and packages throughout the manuscript.

I also recommend that the authors reflect on how their findings advance knowledge in the field. The discussion includes limitations but could be strengthened.

Overall, I was pleased to review the manuscript and believe that, once the authors address the comments, it could be suitable for publication.

Comments for author File: Comments.pdf

Comments on the Quality of English Language

The manuscript is well written, but some sentences are overly complicated, and you could use more direct language. I added specific comments to the PDF, but I also suggest reviewing the entire manuscript to improve clarity.

Author Response

Response to Reviewer 3 Comments

Manuscript ID: sensors-4553923

Title: Handcrafted Features versus Learned Representations for IMU-Based Goat Behavior Classification: Accuracy, Validation Design, and Computational Cost

1. Summary

Thank you very much for taking the time to review this manuscript. We are particularly grateful for the detailed reading and the annotated manuscript. Please find the detailed responses below and the corresponding revisions marked in blue in the resubmitted manuscript. Each response states briefly what was changed and where, followed by the revised text; page and line numbers refer to the revised manuscript. Before the point-by-point responses, we report three corrections that we identified during the revision (Section 2); none of them changes the conclusions.

2. Corrections identified by the authors

“…the mean ± SD of per-subject Macro F1 (n = 15), where each subject’s Macro F1 is averaged over the classes present in its held-out partition.” (Section 2.7, page 12, lines 424–426)

We apologize for these errors. We have also re-checked every citation against its source and revised the wording where it did not match the cited study; these changes are marked in blue as well.

3. Point-by-point response to Comments and Suggestions for Authors

Responses to the general comments are given first (Comments 1–7), followed by the comments in the annotated PDF (Comments 8–57). For the annotations, the page of the originally submitted PDF and the highlighted text are given in parentheses.

3.1 General comments

Comments 1: I recommend that the authors expand their literature search to include relevant literature, particularly on beef bulls, cows, and calves, as well as papers on dairy cows. Studies have implemented or tested approaches similar to those described by the authors. Including them and discussing their findings alongside yours would strengthen the paper and properly place the novelty of your study within the field.

Response 1: Thank you. We agree. We have added five studies in cattle, namely Rahman et al. (2018), Camargo et al. (2024; beef bulls), Riaboff et al. (2020; dairy cows), Vázquez Diosdado et al. (2015; housed dairy cows) and Carslake et al. (2021; dairy calves), and one in goats, Kamminga et al. (2018; collar-mounted sensors). They are cited in the Introduction (paragraphs 1, 2 and 4), for the methodological choices in Sections 2.1–2.3 and in the Discussion (Sections 4.3 and 4.5), for example:

“In ruminants, rumination and eating time are among the most informative behavioral indicators for health surveillance in dairy systems and for health and reproductive monitoring in beef cattle [2,3].” (Introduction, page 2, lines 54–56)

“Statistical and spectral features are extracted from signal windows and, often after feature selection, classified with decision trees or tree ensembles such as random forests, AdaBoost, or gradient boosting [7-10].” (Introduction, page 2, lines 67–69)

“All downstream models were trained and evaluated on raw axis-native signals, which places the burden of orientation invariance on the model and not on a preprocessing pipeline [19].” (Section 2.1, page 4, lines 140–142)

The other passages citing these studies are quoted in Responses 15 (Introduction, paragraph 4), 18 (Section 4.3, paragraph 4), 22 (Sections 2.2 and 4.5), 23 and 24 (Section 2.3) and 50 (Section 4.3).

Comments 2: The authors used a mixed labelling approach (computer-vision and visual observation) for ground truth. A concern is that the company that provided the sensors also provided the computer-vision software. The authors should address this and discuss whether it could introduce data leakage or compounding uncertainty that affects their results.

Response 2: Thank you for raising this concern. We should first clarify that the automatic labeler does not use computer vision: it operates on the IMU signal, and the BoditToolBox software is only an interval-marking tool used by the observers, who worked from the video alone:

“Five trained observers, each responsible for a distinct subset of animals with no overlap, first annotated rumination and eating episodes from the reference video using the BoditToolBox video annotation software (version 1.0, Bodit Co., Ltd., Republic of Korea), an interval-marking tool; the IMU waveform was not shown to the observers.” (Section 2.2, page 4, lines 153–157)

The leakage concern therefore applies to the IMU-based labeler. Section 2.2 now describes its stages and the share of final windows from manual annotation and from the labeler, the video check of 600 retained windows is now reported with Wilson 95% confidence intervals, and Section 4.5 states that the circularity introduced by the labeler’s KNN stage is most relevant to Model A:

The architecture of the manufacturer’s binary screening model is not disclosed, as stated in Section 2.2 (quoted above) and in the Limitations, and the manufacturer’s role is stated, as in the original submission, in the Conflicts of Interest:

“Bodit Co., Ltd. provided the sensor hardware and the labeling pipeline and contributed to data acquisition. The comparison of model architectures reported here, the interpretation of the results, and the decision to publish were determined by the academic authors.” (Conflicts of Interest, page 25, lines 951–954)

Comments 3: No inter-rater reliability is presented to assess the consistency of the labelling over time. The authors should also better describe the observations and the composition of the subsampled data.

Response 3: Thank you. Each animal was annotated by one of five observers with no overlap, so inter-rater reliability could not be computed, and intra-observer consistency over time was not tested either. The first point is now stated in the Methods, and both are stated as a limitation:

“Because each animal was annotated by a single observer, inter-rater reliability could not be computed.” (Section 2.2, page 5, lines 177–178)

“Inter-rater reliability of the manual annotation could not be assessed because each animal was annotated by a single observer, and intra-observer consistency over time was not tested.” (Section 4.5, page 23, lines 847–849)

The only re-examination of the labels against the video was the check of 600 retained windows (Section 2.2, paragraph 3; quoted in Response 2), which agreed with the assigned labels in 99.3% of cases; it indicates the accuracy of the retained labels rather than the stability of individual observers.

The observations are now described in more detail, and Section 2.3 explains the origin of the Other class and the subsampling:

“Five trained observers, each responsible for a distinct subset of animals with no overlap, first annotated rumination and eating episodes from the reference video … This manual stage covered 14 animals over 32 animal-days and yielded 43,119 labeled rumination and eating windows.” (Section 2.2, page 4, lines 153–158)

“It was drawn mainly from the subset of (subject, day) recordings for which annotation covered the full 24-hour period … Seven fully annotated animal-days from six animals contributed the large majority of Other windows, with the remainder drawn from unlabeled intervals of partially annotated animal-days. … Windows of all three classes were then randomly subsampled without replacement (NumPy RandomState, seed = 42) to a comparable per-class count, approximately 44,000 each, giving an aggregate ratio of about 1 : 1 : 1.” (Section 2.3, page 5, lines 201–211)

The number of animals and days is now given in the caption of Table 1 (quoted in Response 27), and the number of windows per subject and class in the new Table S4.

Comments 4: I suggest the authors emphasize the LOSO results rather than the K-fold results, even though the differences are not as significant. LOSO is a significantly more robust validation method and produces more realistic results for this type of data. I suggest the authors refer to dairy cattle studies (some of which were cited by the author, such as Riaboff et al.) to incorporate statistical tests to compare models. GLM models would be more appropriate for many of the comparisons.

Response 4: Thank you. We agree. LOSO is now the primary result: it is reported first in the Abstract, in Tables 4, 5 and 7 and in Figures 5 and 7, Table 9 and Figure 9 have been recomputed on LOSO Macro F1 (quoted in Response 45), and Section 2.7 states why:

“…under leave-one-subject-out (LOSO) and stratified 5-fold cross-validation (CV). A 24-dimensional learned representation matched a 250-dimensional handcrafted feature set (Macro F1 0.810 versus 0.814 under LOSO, 0.876 versus 0.876 under 5-fold CV)…” (Abstract, page 1, lines 35–38)

“Figure 7. Macro F1 as a function of sampling rate for all six models under (a) subject-level LOSO and (b) stratified 5-fold cross-validation.” (Figure 7, page 17, lines 616–617)

“As the appropriate scheme for assessing predictive performance on new animals, LOSO is treated as the primary result.” (Section 2.7, page 11, lines 410–411)

Cattle studies that compared validation designs are now cited in the Introduction and in Section 4.3 (see Response 50). For the model comparison we fitted a linear mixed model, the extension of the general linear model to repeated measures, with subject as a random intercept, because all models were evaluated on the same 15 subjects:

Comments 5: I recommend the authors use computational costs rather than deployment costs. Also, add the programming language and packages throughout the manuscript.

Response 5: Agree. The title now ends “Accuracy, Validation Design, and Computational Cost”, and “computational cost” is used wherever the text refers to what was measured. Package and function names are now given at the main steps of the Methods: for example, NumPy RandomState in Section 2.3 (quoted in Response 3), scikit-learn StratifiedKFold in Section 2.7 and R with lme4 and emmeans in Section 2.11 (quoted in Response 35). Section 2.10, retitled “Reproducibility and Software Environment”, cites each package and gives the versions of Python, PyTorch, LightGBM and scikit-learn:

“Stratified 5-fold cross-validation (5-fold CV) partitions the full dataset into five folds while preserving the class distribution in each (scikit-learn StratifiedKFold, shuffle = True, random_state = 42).” (Section 2.7, page 11, lines 412–414)

“All models were trained and evaluated in an identical software environment: Python 3.12.13, PyTorch 2.11.0 [28] with CUDA 13.0, LightGBM 4.6.0 [21], scikit-learn 1.8.0 [29], NumPy [30], and SciPy [27].” (Section 2.10, page 13, lines 480–482)

Comments 6: I also recommend that the authors reflect on how their findings advance knowledge in the field. The discussion includes limitations but could be strengthened.

Response 6: Thank you. We agree. A paragraph at the end of the Limitations now states what the study contributes relative to the existing literature and what its practical results are:

“Within these limits, the study contributes three things that the existing literature on ruminant behavior classification rarely provides together: a controlled comparison in which feature source, classifier, and training objective are varied one at a time on identical data; window-level and animal-level validation reported side by side on the same dataset, quantifying the inflation that window-level partitioning produces; and the computational and communication costs (feature dimensionality, sampling rate, latency, payload) that determine whether a model can run on a collar. For practitioners the practical results are that a 24-dimensional learned representation is sufficient, that 10–15 Hz sampling retains most of the accuracy, and that among the leading models the choice should be made on update cost and inference pipeline rather than on accuracy differences that do not reach significance.” (Section 4.5, pages 23–24, lines 881–891)

Comments 7: The manuscript is well written, but some sentences are overly complicated, and you could use more direct language. I added specific comments to the PDF, but I also suggest reviewing the entire manuscript to improve clarity.

Response 7: Thank you. The manuscript has been edited throughout for clarity; the wording points raised in the annotated PDF are addressed individually below.

3.2 Comments in the annotated manuscript

Comments 8: (p. 1, Abstract; highlighted: “rarely isolate individual design choices”) Not sure what that means

Response 8: Thank you. We agree that the phrase was unclear and have rephrased it:

“Comparisons of behavior classification pipelines rarely vary one design factor at a time or report computational cost.” (Abstract, page 1, lines 30–31)

Comments 9: (p. 1, Abstract; highlighted: “was far more costly,”) Is costly the correct term to refer to it? What is the cost?

Response 9: Thank you. We agree that “costly” was imprecise and have replaced it with the quantity itself:

“Replacing the supervised training objective with unsupervised reconstruction reduced Macro F1 by 0.094–0.127.” (Abstract, page 1, lines 39–40)

Comments 10: (p. 1, Title; highlighted: “Deployment”) I believe computational cost would be a more appropriate term for what was measured.

Response 10: Agree. The title now ends “Accuracy, Validation Design, and Computational Cost” (see Response 5).

Comments 11: (p. 2, Introduction; highlighted: “that intermittent human observation cannot capture”) This sentence is not correct, and I suggest rephrased it. Intermittent human observation have captured those disruptions for hundreds of years. Continuous monitoring theoretically enable to detect some issues earlier and more precisely than human observations.

Response 11: Thank you. We agree and have rephrased the sentence along the lines suggested:

“The time budgets of key behaviors provide information on animal health and welfare that intermittent human observation captures only coarsely; continuous sensing can detect changes earlier and at finer temporal resolution [1].” (Introduction, page 2, lines 52–54)

Comments 12: (p. 2, Introduction; highlighted: “In ruminants, rumination and eating time are among the most informative behavioral indicators.”) I suggest bring the context here because as it is this sentence is not true. There is many recent studies showing that this behaviour are not relevant for all ruminants. For example, for health issues or productive monitoring in beef cattle. I suggest you revisit recent literature in applied behavioural monitoring of beef bulls and bring the productive context to this sentence.

Response 12: Thank you. We agree that the relevance of these behaviors depends on the production context. The sentence now states the context in which each use is supported and cites a study of beef bulls (Camargo et al., 2024):

Comments 13: (p. 2, Introduction; highlighted: “such estimates may reflect within-animal fit as much as generalization to unseen animals.”) I suggest rephrase this sentence. When instances from the the same animal are in training and test sets you cannot infer generalizability in animal behaviour classification. As the major source of variability is between-animal variability and not within animal-variability, if you does not leave animals out of training you are not testing, you are only validating your model.

Response 13: Thank you. We agree and have rephrased the sentence:

“Because adjacent windows are highly correlated and differences between animals are the main source of variability in behavior classification, such estimates cannot be used to infer generalization to unseen animals [15,16].” (Introduction, pages 2–3, lines 90–93)

Comments 14: (p. 2, Introduction; highlighted: “leave-one-subject-out cross-validation, directly tests the latter”) LOAO is a validation tool, not a testing tool. It does not test generalization because you don’t have a final model (trained and stable) tested in animals new animals. Please rephrase this sentence.

Response 14: Thank you. We agree and have adopted this terminology: the Introduction no longer describes LOSO as a test, Section 2.7 states what LOSO does and does not evaluate, and “test set” and “test partition” have been replaced by “validation partition” or “held-out partition” throughout:

“Subject-level validation, such as leave-one-subject-out cross-validation, estimates this generalization directly.” (Introduction, page 3, lines 93–94)

“…has no subject-level leakage and estimates how the training procedure generalizes to unseen individuals; it does not evaluate a single fixed model on new animals, and its estimates are comparisons among models under matched conditions, not field accuracy.” (Section 2.7, page 11, lines 407–410)

Comments 15: (p. 2, Introduction; highlighted: “rarely compared on the same dataset”) Rahman et al (2018) performed this exactly comparison that informed several studies in the field. I suggest you review this and incorporate this paper in your intro and discussion. 10.1016/j.inpa.2017.10.001

Response 15: Thank you for this reference. Rahman et al. (2018) is now introduced in the Introduction, and the statement has been corrected:

“Rahman et al. [16] compared within-animal and across-animal partitioning on the same cattle dataset and reported a marked reduction in accuracy under the latter. Since then, however, subject-level validation has remained less common, and few studies have reported both schemes on the same dataset [17,18].” (Introduction, page 3, lines 94–97)

The study is also compared with our results in Section 4.3 (see Response 50).

Comments 16: (p. 3, Section 2.1; highlighted: “such as quaternions or rotation matrices. The only signal transformations applied were the per-channel z-score normalization of Section 2.6 and, for the sampling-rate experiments, the resampling of Section 2.8.”) I suggest remove this entire excerpt. This is part of your preprocessing and stating that the raw data served as the model input is enough.

Response 16: Agree. The excerpt has been removed:

“The raw six-channel time series as delivered by the logger served as the model input in every downstream experiment.” (Section 2.1, page 3, lines 128–129)

Comments 17: (p. 3, Figure 1) I suggest add in the figure the direction of axis in relation to the animals body.

Response 17: Thank you. We agree. Figure 1 now shows the orientation of the sensor axes relative to the animal’s body, and Section 2.1 defines them. In preparing the figure we found that the axis assignment in the original Section 2.1 was incorrect: gravity is carried by the X axis, which runs along the collar strap, not by the Y axis. The sentence has been corrected; no result depends on it, because all models received the raw axis-native signals.

“Figure 1. Wearing position of the collar-mounted six-axis IMU on a Korean black goat and orientation of the sensor axes relative to the body: (a) left lateral view; (b) cross-section of the neck at the collar, cranial view. Arrows indicate the positive axis directions; ⊙ indicates an axis pointing toward the viewer.” (Figure 1, page 4, lines 132–135)

Comments 18: (p. 4, Section 2.1; highlighted: “small subject-specific orientation offsets.”) Was that measured to state that this is small? If not I suggest remove the word small. Also, the rotation is usually temporary and not consistent across individuals. Were there individuals with the collar rotated over the entire experimental period or they fixed position after a while? If so this should be noted, otherwise you should recognize that this rotation was temporary.

Response 18: Thank you. The offsets were not measured, so “small” has been removed and the sentence now states that they were not quantified:

“Collar rotation between individuals and micro-drift during movement introduce subject-specific orientation offsets, which were not quantified.” (Section 2.1, page 4, lines 138–139)

Collar position was not recorded over time, so we cannot say whether rotation was temporary or persistent in individual animals, and the revised sentence does not assert either. Its possible contribution to between-animal variation is discussed in Section 4.3, with a reference on orientation-independent features for collar-mounted sensors in goats:

“The models received the native IMU axes without per-subject orientation calibration, so differences in collar fit, resting orientation, and movement-induced rotation can generate animal-specific offsets [19].” (Section 4.3, page 21, lines 774–776)

Comments 19: (p. 4, Section 2.2; highlighted: “cameras,”) Report the camera model for reproducibility.

Response 19: Agree. The camera model and recording settings have been added:

“Reference video was captured by ceiling-mounted internet protocol cameras (Roboview 24-3, Global I-net, Gwangmyeong, Republic of Korea; 1920 × 1080, approximately 30 fps), one camera per pen, covering the full floor area with no blind zones.” (Section 2.2, page 4, lines 144–146)

Comments 20: (p. 4, Section 2.2; highlighted: “Video and IMU timelines”) If the cameras were connected to Internet their time drift was close to none. However the devices were not, so there was time drift. The fact that no time drift correction was applied to IMU data should be stated.

Response 20: Thank you. We agree. The paragraph now states how often the timelines were aligned, how IMU timestamps are generated, that no drift correction was applied, and the resulting bound on drift:

“Video and IMU timelines were aligned manually at the start of each 30-minute recording session. IMU timestamps are generated on the logger with a per-sample sequence number and are therefore unaffected by transmission latency. No clock-drift correction was applied; because alignment was repeated every 30 min, accumulated drift remains below 0.2 s even for a 100-ppm oscillator, under 2% of a 10-s window.” (Section 2.2, page 4, lines 146–151)

Comments 21: (p. 4, Section 2.2; highlighted: “Ground-truth labels for the two focal behaviors, rumination and eating, were established through a semi-automatic annotation procedure. Trained observers first annotated a seed set of rumination and eating episodes from the reference video … Agreement between the automatic labels and the human video assessment was 99.3% overall (Rumination 98.5%, Eating 99.5%, Other 100.0%).”) This can be highly problematic and should be adequately stated in the objectives, and discussed as a limitation of the study. The fact that the ground-truth labels were mostly generated by a video classifier provided by the same company that created the IMU could be a relevant interest conflict. In addition you are including a new source of uncertainty in your data (as all models hold some uncertainty degree). I highly suggest at the very least to mention in your objectives and abstract that the ground-truth labels were mostly obtained by a video classifier. I also suggest you also state as a limitation and discuss this in the discussion section.

Response 21: Thank you. We agree that the origin of the labels must be stated clearly. As explained in Response 2, the automatic labeler is not a video classifier: it operates on the IMU signal, only the human observers used the video, and the manufacturer’s role is stated in the Conflicts of Interest. Of the final windows, 58.9% come directly from manual video annotation and 41.1% from the automatic labeler. The label origin is now stated in the Abstract and the objectives, and the first limitation in Section 4.5 now gives the share of automatically assigned windows and the resulting circularity:

“…with labels from a semi-automatic procedure verified against synchronized video.” (Abstract, page 1, lines 32–33)

Comments 22: (p. 4, Section 2.2; highlighted: “This criterion also limits the influence of any residual timeline misalignment, since an offset of a few seconds affects at most the first and last 10 s window of each episode.”) On the other hand this is also a limitation of the model, as in real life animal can express bouts of rumination and eating shorter than 180s. In those cases you don’t know how your model will perform. Others have done the same in beef bulls, beef calves, and beef cows, so it is not a enormous limitation but should be recognized. I suggest incorporate the relevant literature here (to support your decision) and discuss this as a limitation in the appropriate section.

Response 22: Thank you. We agree. The criterion is now supported by the study of beef bulls by Camargo et al. (2024), in which very short bouts were also removed, and the corresponding limitation in Section 4.5 now also states what happened to the shorter episodes and cites this study:

“Only episodes lasting at least 180 s were retained as valid events; very short bouts have likewise been removed in beef bulls, in which they were poorly represented by window-level features [3].” (Section 2.2, page 5, lines 181–184)

“Shorter episodes were not discarded but were treated as Other, so the residual class contains a small proportion of brief feeding and rumination bouts. The dataset therefore emphasizes sustained, clearly defined episodes and does not characterize performance on short, fragmented, or transitional events, which are likely the most difficult cases in continuous operation [3].” (Section 4.5, page 23, lines 851–855)

Comments 23: (p. 4, Section 2.3; highlighted: “Windows containing more than one behavior class were excluded, so each retained window carries a single unambiguous label.”) Once again, there is literature to support these decision in sheep and beef bulls so I suggest referencing to it here. It should also be mentioned as a limitation as in real life those events exist.

Response 23: Thank you. In the studies we could verify, in beef bulls (Camargo et al., 2024) and beef calves (Kim et al., 2024), such windows were retained and assigned to the prevailing behavior rather than excluded; we now cite them as the alternative approach:

“Windows containing more than one behavior class were excluded, so each retained window carries a single unambiguous label; studies in beef bulls [3] and beef calves [11] instead assigned such windows to the prevailing behavior.” (Section 2.3, page 5, lines 197–199)

We kept the exclusion so that every window in the comparison of feature representations carries an unambiguous label. The resulting limitation, that windows spanning a transition are not characterized, is stated in Section 4.5 (paragraph 2; see Response 22).

Comments 24: (p. 4, Section 2.3; highlighted: “10”) Why 10s? There is plenty literature yo support this decision, some of which you already cites throughout the paper. I suggest include these references here.

Response 24: Thank you. We agree. The choice is now supported by references:

“Window length affects classification accuracy [20]; 10 s is the median window length among accelerometer studies of ruminant behavior [6] and has been used in dairy cows [7] and beef calves [11].” (Section 2.3, page 5, lines 191–194)

Comments 25: (p. 4, Section 2.3 title; highlighted: “Construction”) You refer to some Python packages (pytorch, numpy) when describing training so I supose this was all done in Python. But you make no reference to any other package or even programming language used. I reccomend specify programing language (with version) and all packages used at every step.

Response 25: Agree. Package and function names are now given at the main steps of the Methods, and Section 2.10 gives the language, the versions and the references (see Response 5).

Comments 26: (p. 5, Section 2.3; highlighted: “subsampled to”) Include here you subsampling criteria and package/library used. Were these epochs randomly selected? Did you balanced per subject per day? How much of those represent the manual label epochs an dhow much was comp. vision classification? Include relevant information to ensure reproducibility.

Response 26: Thank you. Windows were selected at random without replacement using NumPy with a fixed seed (Section 2.3, paragraph 2; quoted in Response 3). Balancing was applied at the class level only, not per subject or per day; the resulting numbers of windows per subject and class, with the recording days per subject, are given in the new Table S4. The shares of manual and automatic labels are now reported:

“Of the 132,887 windows in the final dataset, 78,320 (58.9%), including Other windows, originated directly from manual annotation and 54,567 (41.1%) from the automatic labeler.” (Section 2.2, page 5, lines 170–172)

Comments 27: (p. 5, Table 1; highlighted: “Final dataset composition”) Final dataset composition correspond to the data after subsampling? Oh how many animals over how many days? Tables and figures should stand alone from the text. I suggest add more details in the table title. e.g., Final dataset composition of retained per-class counts after balancing subsampling processing of XX animals over xx days. Each sample correspond to 10s time-windows.

Response 27: Agree. The caption has been revised as suggested:

“Table 1. Final dataset composition: retained per-class counts of 10-s windows after high-confidence filtering and class-balancing subsampling, from 19 Korean black goats over nine recording days.” (Table 1, page 5, lines 215–216)

Comments 28: (p. 5, Section 2.4.2; highlighted: “Model A”) Why use LightGBM in such a high dimentional input of 250 features? LightGBM are much more prone to overfit than XGB for example. I suggest add a couple of sentences justifying your choices of LGB and KNN as well.

Response 28: Thank you. We agree and have added a justification of LightGBM:

“LightGBM was retained because Model A reproduces the pipeline of Kim et al. [11], in which it was the final classifier. With about 133,000 windows, and with row and column subsampling (bagging_fraction = 0.8, feature_fraction = 0.8) acting as regularization, over-fitting of leaf-wise tree growth is limited.” (Section 2.5, page 10, lines 363–366)

KNN is used in Model C as a non-parametric probe of the learned representation, as already stated where Model C is introduced:

“Model C tests whether the representation retains discriminative structure under a non-parametric classifier that applies no additional feature weighting.” (Section 2.4.3, page 8, lines 301–302)

Comments 29: (p. 6, Section 2.4.3; highlighted: “Models B and C”) Define Models B and C here. e.g., used in models B (LightGBM downstream classifier) and C (KNN downstream classifier).

Response 29: Agree. The sentence now reads as suggested:

“Models B (LightGBM downstream classifier) and C (KNN downstream classifier) share a hierarchical three-level feature extractor that maps a raw IMU window of size 250 × 6 to a 24-dimensional learned representation (Figure 3).” (Section 2.4.3, page 7, lines 251–253)

Comments 30: (p. 8, Section 2.4.6; highlighted: “LightGBM classifiers are not included in these estimates”) Why are they not included in these estimates. If computational cost is an important measure for your study should you have comparable metrics among different classifiers?

Response 30: Thank you. Model size in Table 2 is estimated from neural-network parameter counts, and a tree ensemble has no comparable parameter count. We agree that the classifier stage matters for computational cost: the latency measurements include it, with its share now reported, and Section 4.4 now discusses its likely memory footprint relative to the extractor, which was not measured:

“Model B latency covers the deep-learning feature extractor forward pass and LightGBM prediction, the latter contributing 0.12–0.18 ms.” (Section 2.9, pages 12–13, lines 461–463)

“The tree-ensemble stage of Models B and E, by contrast, comprises up to 1,500 trees of 63 leaves and would likely occupy more memory than the extractor itself, so the end-to-end design of Model D is the more natural candidate for on-collar inference, whereas the modular designs suit gateway- or server-side inference where the classifier can be refitted cheaply.” (Section 4.4, page 22, lines 820–824)

Comments 31: (p. 8, Table 2 notes; highlighted: “Params refers to neural network parameters; model size is estimated as Params × 4 bytes … For Model D, which classifies internally, the Features column reports the dimensionality of the pooled summary vector rather than of an externally exposed feature vector”) Organize this as a proper footnote linking the explanations of acronyms and names in teh columns to the proper explanation. Use the journal guidelines to ensure you use adequate format (eg., superscribed numbers or letters, etc.)

Response 31: Agree. The notes have been reorganized as a general note followed by lettered footnotes (a–c) attached to the cells they explain:

“Params, neural network parameters; model size is estimated as Params × 4 bytes (32-bit floating point) and excludes the LightGBM classifier.” (Table 2, page 9, lines 346–347)

“^a Model A uses LightGBM alone, whose parameterization is not comparable to neural network parameter counts.” (Table 2, page 9, lines 348–349)

“^b Dimensionality of the pooled summary vector; Model D classifies internally and exposes no feature vector.” (Table 2, page 9, lines 350–351)

“^c Includes the decoder used during reconstruction training; the decoder is discarded at inference, so the deployed encoder matches Model E at approximately 40K parameters.” (Table 2, page 9, lines 352–353)

Comments 32: (p. 9, Section 2.5; highlighted: “LightGBM classifier”) Was any hyperparameter tunning performed in LGBM or KNN? If not, why? Were this hyperparameters came from?

Response 32: Thank you for these questions. No tuning was performed for either classifier. The values were not taken from Kim et al. (2024), who tuned their classifier for calf data with Optuna. Instead, a single configuration was fixed a priori and applied unchanged to Models A, B, E and F (Table 3: learning rate 0.05, 63 leaves, row and column subsampling of 0.8, at most 500 boosting rounds with early stopping), and the KNN classifier of Model C used k = 5 and Euclidean distance (Section 2.5, last paragraph). The reason for not tuning is now stated:

“The hyperparameters of both classifiers were fixed a priori (Table 3) and not tuned for any model, because tuning the classifier separately for each feature representation would confound the feature-extraction contrast that the design is meant to isolate.” (Section 2.5, page 10, lines 367–369)

Comments 33: (p. 10, Section 2.7; highlighted: “It is retained here because it remains widely used in this literature and provides a reference point for published figures obtained under comparable partitioning.”) K-fold is not the standard method for validation in animal behaviour classification. If you decide to keep it here to make it easier to compare with other papers you should state that but you should also mention at some point that for any predictive performance assessment of models the LOSO should be used.

Response 33: Thank you. We agree. Section 2.7 already gave the reason for retaining 5-fold CV; it now also states that LOSO is the appropriate scheme for assessing predictive performance and that 5-fold estimates cannot be used to infer generalization to unseen animals:

“As the appropriate scheme for assessing predictive performance on new animals, LOSO is treated as the primary result.” (Section 2.7, page 11, lines 410–411)

“Such estimates cannot be used to infer generalization to unseen animals; they estimate an upper bound on the representational capacity of each model under within-subject sampling.” (Section 2.7, page 11, lines 416–418)

Comments 34: (p. 10, Section 2.7; highlighted: “test”) Validation partition. You did not test your model, you only validated them.

Response 34: Agree. “Test” has been replaced by “validation partition” or “held-out partition” throughout (see Response 14), for example:

“Leave-one-subject-out (LOSO) validation holds out all data from a single subject as the validation partition and trains on the remaining subjects, cycling through all subjects.” (Section 2.7, page 11, lines 400–401)

Comments 35: (p. 10, Section 2.7 title; highlighted: “Validation”) A section should be added to report the inference tests you used to compare models.

Response 35: Agree. A new Section 2.11 (Statistical Analysis) has been added:

“Models were compared on per-subject Macro F1 under LOSO at 25 Hz, averaged over the classes present in each subject’s held-out data, with each held-out subject as the experimental unit (n = 15). A linear mixed model was fitted with model (A–F) as a fixed effect and subject as a random intercept, using R version 4.6.1 [31] and the lme4 package [32]. Estimated marginal means and Tukey-adjusted pairwise contrasts with 95% confidence intervals were obtained with the emmeans package [33], and paired Cohen’s d_z is reported as the effect size for the contrasts discussed in the text. Fold-level differences under 5-fold CV were not tested, because folds are resamples of a single dataset rather than independent experimental units.” (Section 2.11, page 13, lines 489–497)

Comments 36: (p. 11, Section 2.8; highlighted: “The top-250 feature”) I suggest that the name and feature importance of these 250 features to be added as supplemental materials.

Response 36: We thank the reviewer for this suggestion. We have not added the list: the 250 features are indices into a combinatorially generated set of 903 candidates, and Model A serves to reproduce the pipeline of Kim et al. (2024) as a baseline rather than to interpret individual features. The feature families are described in Section 2.4.2, and the full list with importance values is available from the corresponding author on request.

Comments 37: (p. 11, Section 2.8; highlighted: “reused at all lower rates”) Have you tested whether selecting features for the appropriate sampling rates rather reuse them change your conclusions?

Response 37: Thank you. We did not re-select features at each rate. As in the original submission, Model A’s values below 25 Hz are treated as a conservative estimate for this reason (Section 3.4, paragraph 2), and Section 3.4 now also states that the low-rate difference between Models A and B favors Model A:

Re-selection would therefore be expected to widen this difference rather than reverse it. The cost of reduced sampling was also of similar size in Models B, D and E, which do not use the selected indices, so the conclusions about the learned representations and the 10–15 Hz operating point are unaffected:

Comments 38: (p. 12, Section 2.9; highlighted: “Python/NumPy”) Review all applications of packages throughout the paper and make the proper reference to them. This is not the standard in scientific literature.

Response 38: Agree. The software is now cited: PyTorch, scikit-learn and NumPy in Section 2.10, which also gives the versions of Python, PyTorch, LightGBM and scikit-learn (quoted in Response 5), and R, lme4 and emmeans in Section 2.11 (quoted in Response 35). LightGBM and SciPy were already cited at first use (Sections 2.4.2 and 2.8).

Comments 39: (p. 12, Section 2.10; highlighted: “2.10.”) This description should be either a the beginning of MM or spread across the MM when you first refer to the packages as steps involving them.

Response 39: Thank you. We followed the second option: package and function names are now given at the main steps where they are used (see Response 5). Section 2.10, retitled “Reproducibility and Software Environment”, is kept as a short summary of the computing environment to which the latency measurements refer.

Comments 40: (p. 12, Section 3.1; highlighted: “Table 4 summarizes the classification performance of the six models under both validation schemes.”) Move this sentence to line 482

Response 40: Agree. The sentence has been moved to the end of Section 3.1, immediately before Table 4:

“Table 4 summarizes the classification performance of the six models under both validation schemes.” (Section 3.1, page 14, lines 530–531)

The same change has been made in the other Results sections listed in Response 43.

Comments 41: (p. 13, Section 3.2; highlighted: “The spread between the highest- and lowest-scoring model widened monotonically with class difficulty:”) Rephrase this sentence. What do you mean by class difficulty? This is the first time you used this term which seems to be a subjective rank of the authors.

Response 41: Thank you. We agree. “Class difficulty” is now defined at first use by the per-class F1 attained across models:

“All six models produced the same ordering of class difficulty, defined here by the per-class F1 attained across models: Eating highest, Rumination intermediate, and Other lowest.” (Section 3.2.1, page 14, lines 539–541)

Comments 42: (p. 14; highlighted: “→”) Replace all “→” by “to” in the text. This is acceptable when referring to steps in a written diagram but it is not acceptable when referring to a interval of values.

Response 42: Agree. Value ranges are now written with “to” or an en dash, for example:

“For Models A and B the 5 to 10 Hz step accounted for more than half of the total 5 to 25 Hz gain, while 20 to 25 Hz contributed no more than 0.003. Across Models A–E the total 25 to 5 Hz reduction ranged from 0.022 (Model A) to 0.043 (Model C) under 5-fold CV.” (Section 3.4, page 16, lines 595–598)

Arrows are retained only for pipeline steps (Figure 2 caption, architecture descriptions and equations) and for the contrast labels in Table 7.

Comments 43: (p. 15, Section 3.5; highlighted: “Table 8 and Figure”) As mentioned above if you refer to the tables and figures at the beginning of the section it is likely that they will placed here instead of after the following text. I suggest move this to line 580 and make the same change across you results section.

Response 43: Agree. The reference has been moved to the end of Section 3.5, and the same change has been made in Sections 3.1, 3.2.1, 3.2.2 and 3.4 and for Table 9 in Section 3.6:

“Per-sample latencies at batch size 1 are given in Table 8 and Figure 8.” (Section 3.5, page 17, line 632)

Comments 44: (p. 16, Section 3.6; highlighted: “1,000 animals”) Where these values come from if you enrolled 19 animals in your study? If this is a simulation you should report the values you found with your animals and describe in the MM section the simulation parameters and how you did. I don’t see any value in scaling up your results. I suggest you report data per animal per day instead.

Response 44: Thank you. We agree. The scaled-up figure has been removed, and the section now reports CPU time per animal-day, derived from the measured per-window latencies:

“Under continuous monitoring, each animal generates 8,640 windows per day. At the measured per-window latencies, processing one animal-day at 25 Hz corresponds to 373 s of single-thread CPU time for Model A, 23 s for Model B, and 13 s for Model D.” (Section 3.6, page 18, lines 642–644)

Comments 45: (p. 16, Section 3.6; highlighted: “Speed–Accuracy Trade-off and Aggregate Reduction”) LOSO results should be reported instead of K-fold or at least reported alongside to K-fold. Once more, LOSO are significantly more realistic for this type of data so it should prioritized over K-fold.

Response 45: Agree. Figure 9 and Table 9 have been recomputed on LOSO Macro F1:

“Figure 9. LOSO Macro F1 against throughput for Models A, B, and D across all sampling rates (batch = 1).” (Figure 9, page 18, lines 647–648)

“Δ is the change in LOSO Macro F1 relative to the Model A 25 Hz reference.” (Table 9, page 19, line 658)

Comments 46: (p. 19, Section 4.3; highlighted: “The two validation schemes produced systematically different estimates for every model, with aggregate Macro F1 falling by 0.044–0.095 from 5-fold CV to LOSO. The inflation follows from how windows are assigned to folds. Allocation is independent of subject identity and temporal position, so data from a single animal appear in both partitions”) Revise this excerpt. It’s not clear what “The inflation follows from how windows are assigned” means. “Falling by xx-xx from xx-xx” is also odd. You must be clear that the last sentence only apply for K-fold.

Response 46: Thank you. We agree. The excerpt has been rewritten to state the mechanism and to make clear that it applies to 5-fold CV:

“The two validation schemes produced systematically different estimates for every model, with aggregate Macro F1 decreasing by 0.044–0.095 from 5-fold CV to LOSO. This inflation under 5-fold CV arises from window-level partitioning: allocation is independent of subject identity and temporal position, so data from a single animal appear in both partitions.” (Section 4.3, page 20, lines 729–733)

Comments 47: (p. 19, Section 4.3; highlighted: “The annotation criterion compounds the effect: because only bouts of at least 180 s were retained, each contributes at least eighteen consecutive 10-s windows, and shuffling distributes windows from one bout across both partitions”) This should be discussed as a potential limitation of the model and compare with the literature that did the same or not.

Response 47: Agree. The criterion is now supported by the literature, and the limitation in Section 4.5 now also states what happened to shorter episodes (Section 2.2, paragraph 4, and Section 4.5, paragraph 2; both quoted in Response 22). Section 4.3 compares the resulting inflation with cattle studies that reported both window-level and animal-level validation (see Response 50).

Comments 48: (p. 19, Section 4.3; highlighted: “falling”) Replace falling by decreased xx

Response 48: Agree. Replaced by “decreasing by” (Section 4.3, paragraph 1; see Response 46).

Comments 49: (p. 19, Section 4.3; highlighted: “in cattle instrumented at the same neck position and sampling rate.”) Rephrase this sentence. e.g., “…in cattle equipped with collars in similar position and sampling rate as the present study” if that is what you meant.

Response 49: Thank you; that is what we meant. In checking the source, we found that the sensors in Wang et al. were described as attached to the neck, without mention of a collar, and that the values we had cited came from the preprint of that study. The sentence now states the placement and sampling rate explicitly and gives the values of the published article:

“…Wang et al. [15] reported Macro F1 decreasing from 0.89–0.94 under hold-out validation to 0.64–0.76 under leave-cow-out validation in beef cows fitted with neck-mounted accelerometers sampled at 25 Hz, as in the present study.” (Section 4.3, page 21, lines 742–744)

Comments 50: (p. 19, Section 4.3; highlighted: “As reported in Section 3.1, variation between folds was near zero, whereas variation between held-out subjects was two orders of magnitude larger.”) As expected since LOSO is the less inflated CV technique for this type of data. This was describe by many studies in the past I suggest incorporating the relevant literature in beef and dairy cattle to this discussion.

Response 50: Agree. This discussion now includes the cattle literature, and the magnitude in the highlighted sentence has been corrected to “one to two orders of magnitude”:

“Variation between folds was near zero, whereas variation between held-out subjects was one to two orders of magnitude larger.” (Section 4.3, page 21, lines 747–749)

“Between-individual variation of this magnitude is consistent with earlier reports in goats [18] and cattle [15,16], and its dominance carries two consequences.” (Section 4.3, page 21, lines 779–780)

Comments 51: (p. 19, Section 4.3; highlighted: “The two quantities are not directly comparable: the first is the variation of an aggregate estimate across resamples, the second the dispersion of individual units.”) I don’t agree with this statement. In the sense that you are inferring predictive performance of different models (which is one objective of the study) they are completely comparable.

Response 51: Thank you. We accept this point. The sentence has been replaced by the point we intended to make:

“Fold-to-fold variation contains no between-animal information, because every fold draws windows from every subject; it therefore cannot inform generalization to new individuals.” (Section 4.3, page 21, lines 749–751)

Comments 52: (p. 20, Section 4.3; highlighted: “so its aggregate advantage rests disproportionately on subjects contributing more test windows.”) For this reason you should report the distribution of individual and days of you balanced dataset. If they are also balanced per individuals you could isolate this possibility.

Response 52: Thank you; this comment led to a correction. The new Table S4 reports the number of windows per subject and class, with the recording days per subject: windows are not balanced across subjects, and Other windows come from eight of the 15 LOSO subjects. In compiling it we found that the previous per-subject statistic had assigned the other seven subjects an F1 of zero for the absent class; this has been corrected (see Section 2 above). After the correction the rankings by aggregate and by per-subject Macro F1 still differ, but by margins well within the confidence intervals of the mixed model, so we no longer attribute the difference to a particular mechanism and have replaced the highlighted sentence:

“…because the Other class came mainly from seven fully annotated animal-days, seven of these subjects contributed no Other windows.” (Section 2.7, page 11, lines 403–405)

“The ranking by aggregate Macro F1 (Model D first) and by per-subject mean (Model A first) differed, but by margins well within these confidence intervals.” (Section 4.3, page 21, lines 770–772)

Comments 53: (p. 20, Section 4.3; highlighted: “Each subject was also annotated by a single observer without overlap, so systematic differences in annotation practice are absorbed into the same term.”) However, no inter-rater reliability test is reported to check whether raters agree with their assessment over time. This should be discussed as a potential limitation.

Response 53: Agree. As explained in Response 3, inter-rater reliability could not be computed and intra-observer consistency over time was not tested; both are now stated as a limitation:

Comments 54: (p. 21, Section 4.5; highlighted: “Reported metrics should be read as comparisons among models under matched conditions, not as estimates of field accuracy.”) This great and should be stated much earlier in the paper. I suggest add similar statement in the MM section so you avoid readers thinking you are over interpreting your results later on.

Response 54: Thank you. We agree. A similar statement now appears in the Methods:

“…it does not evaluate a single fixed model on new animals, and its estimates are comparisons among models under matched conditions, not field accuracy.” (Section 2.7, page 11, lines 408–410)

Comments 55: (p. 21, Section 4.5; highlighted: “Three directions”) I recommend you reflect on the application of your studies and how your results advance the knowledge in the field.

Response 55: Agree. A paragraph on the contribution and practical implications of the study has been added immediately before this paragraph (Section 4.5, paragraph 5; quoted in Response 6).

Comments 56: (p. 22, Conclusions; highlighted: “Figures obtained under window-level partitioning, here and in the wider literature, are better read as estimates of representational capacity than of expected field performance.”) So what is the point if the ultimate goal of ML models is the have high and generalizable predictive performance?

Response 56: Thank you for this question. Window-level figures are not a basis for model selection; the sentence now states why they are reported:

“Window-level figures should therefore not be used for model selection or for claims about performance on new animals; they are reported here to quantify the inflation and to allow comparison with published results obtained under the same partitioning.” (Section 5, page 24, lines 912–915)

Comments 57: (p. 22, Conclusions; highlighted: “Operational properties therefore provide a more practical basis for model selection when accuracy differences are small”) Are they realistic though?

Response 57: Thank you for this question. We have made the operational properties concrete and stated their limits. Section 4.4 now reports a measured update cost with the assumption behind it and discusses the path to a microcontroller, and the Conclusions name the properties and qualify the latency evidence:

“A PyTorch model cannot execute directly on a Cortex-M-class device; the usual path is export to ONNX followed by conversion to an embedded runtime such as TensorFlow Lite Micro or CMSIS-NN, with 8-bit quantization. … Measured latency on the target device, and the corresponding power draw, remain to be established.” (Section 4.4, page 22, lines 815–825)

“Where accuracy cannot separate models, operational properties such as update cost, inference pipeline, and transmitted payload provide a more practical basis for selection; the latency figures reported here characterize relative computational cost on workstation hardware and await confirmation on target devices.” (Section 5, page 24, lines 917–921)

We hope that the revised manuscript addresses your concerns, and we thank you again for your time and helpful comments.

Sincerely,

Na-Yeon Kim, on behalf of all authors

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

After modification, the paper has identified the key issue of “24 dimensional learning representation classification accuracy comparable to 250 dimensional manually designed feature sets” through two sets of feature extractors with different architectures. The independently supplemented work content makes the conclusions of the paper more accurate. I hope the author can further improve based on the following three suggestions.

A core practical contribution of this paper is evaluating computational cost for collar‑deployed animal monitoring. However, all latency measurements are performed on workstation CPU/GPU instead of real embedded microcontroller hardware. Quantization overhead, flash/RAM footprint for LightGBM tree ensemble are only qualitatively discussed. Conclusions about “Model D is more suitable for on‑collar inference” are speculative without real hardware profiling. If embedded measurement cannot be done, please weaken deterministic deployment statements and clearly state workstation‑measured speed‑up ratios only represent relative comparison between models instead of real‑world edge‑device performance.
Non‑deterministic GPU execution can produce Macro‑F1 shifts up to 0.003, which is comparable to the smallest performance gap (0.0048) between Model A and Model B under LOSO. However, all LOSO results are based on single run. Authors should repeat full LOSO experiments ≥5 times to report mean, standard deviation and confidence intervals for Macro‑F1 of each model, to separate run‑to‑run stochastic fluctuation from true model differences.
Section 4.2 hypothesizes that MSE‑based autoencoder (Model F) prioritizes high‑amplitude eating signals and ignores small‑amplitude rumination chewing pulses, leading to degraded classification performance. This mechanistic explanation is purely post‑hoc speculation without supporting experiments. Authors are encouraged to provide feature visualization (comparing activation patterns of supervised Model E vs unsupervised Model F for eating / rumination / other samples).

Comments for author File: Comments.docx

Author Response

Response to Reviewer 1 Comments

Manuscript ID: sensors-4553923

Title: Handcrafted Features versus Learned Representations for IMU-Based Goat Behavior Classification: Accuracy, Validation Design, and Computational Cost

1. Summary

Thank you very much for your further comments on the revised manuscript. Please find the detailed responses below and the corresponding revisions marked in blue in the resubmitted manuscript. Before the point-by-point responses, we report one correction that we identified while preparing the repeated runs requested in Comment 2 (Section 2); it does no change any reported value.

2. Correction identified by the authors

While preparing the repeated runs, we found that Section 2.6 described two exceptions to the shared training protocol that had been used only in preliminary experiments: a cosine schedule with T_max = 50 epochs and an early-stopping patience of 7 epochs for Model D, and early stopping on the training loss for Model E. All results reported in the manuscript were obtained with the shared protocol for all neural networks. We have removed the two sentences, the clause in the note to Table 7 stating that the E → F contrast differed in early-stopping criterion, and the corresponding sentence in Section 4.2. No reported value changes, and the E → F contrast now differs only in the training objective:

“The neural networks of Models B–F all followed this protocol, except that Model F is trained with mean squared error reconstruction loss instead of Focal Loss, consistent with its unsupervised autoencoder objective.” (Section 2.6, page 11, lines 390–392)

“Training data and evaluation protocol are identical within each contrast.” (Table 7, page 16, line 594)

“Because the decoder is discarded at inference, the two pipelines are computationally equivalent, and they were trained under the same protocol apart from the loss.” (Section 4.2, page 20, lines 716–717)

We apologize for this error.

3. Point-by-point response to Comments and Suggestions for Authors

Comments 1: A core practical contribution of this paper is evaluating computational cost for collar‑deployed animal monitoring. However, all latency measurements are performed on workstation CPU/GPU instead of real embedded microcontroller hardware. Quantization overhead, flash/RAM footprint for LightGBM tree ensemble are only qualitatively discussed. Conclusions about “Model D is more suitable for on‑collar inference” are speculative without real hardware profiling. If embedded measurement cannot be done, please weaken deterministic deployment statements and clearly state workstation‑measured speed‑up ratios only represent relative comparison between models instead of real‑world edge‑device performance.

Response 1: Thank you. We agree that the workstation measurements do not establish performance on embedded hardware, and that the memory footprint of the tree ensemble and the effect of quantization were discussed only qualitatively. On-device profiling was not possible within this revision. We have therefore replaced the statement that Model D is the more natural candidate for on-collar inference with a conditional one, stated which quantities were not measured, qualified the speed-up in the Abstract as a workstation measurement, and retitled Section 4.4 “Computational Trade-offs in Model Architecture and Sampling Rate”:

“At that precision the 21K-parameter extractor of Model B would occupy roughly 21 KB and the 32K-parameter network of Model D roughly 32 KB of parameter memory, within the flash budget of common Cortex-M4/M7 parts. The tree-ensemble stage of Models B and E, by contrast, comprises up to 1,500 trees of 63 leaves and may occupy more memory than the extractor itself. If so, an end-to-end design such as Model D would be easier to fit on a microcontroller, whereas the modular designs may be better suited to gateway- or server-side inference, where the classifier can be refitted cheaply; neither the memory footprint of the tree ensemble nor the accuracy cost of quantization was measured here.” (Section 4.4, page 22, lines 819–827)

Section 2.9 already states, unchanged, that the speed-up ratios represent a relative comparison between models, and the Conclusions that they await confirmation on target devices:

Comments 2: Non‑deterministic GPU execution can produce Macro‑F1 shifts up to 0.003, which is comparable to the smallest performance gap (0.0048) between Model A and Model B under LOSO. However, all LOSO results are based on single run. Authors should repeat full LOSO experiments ≥5 times to report mean, standard deviation and confidence intervals for Macro‑F1 of each model, to separate run‑to‑run stochastic fluctuation from true model differences.

Response 2: Thank you for this suggestion. We repeated the full LOSO protocol at 25 Hz for all six models with six training seeds (42–47), keeping the dataset, the subjects and the code unchanged. The standard deviation of aggregate Macro F1 across runs was 0.0005–0.0037, against between-subject standard deviations of 0.12–0.17. The repeated runs also showed that the smallest gap is larger than run-to-run variation: Model B was below Model A in all six runs (mean difference 0.0054, 95% CI 0.0030–0.0079). Refitting the mixed model to each run nevertheless reproduced the result reported in the manuscript in every run, with no significant contrast among Models A, B, D, and E and Model F below every other model. This small difference is therefore reproducible for these 15 animals, but it does not indicate which model would perform better on new animals. The six-run mean ± SD is now given in Table 4, the per-run values with 95% confidence intervals in the new Table S5, and the analysis is described in Section 2.11; the values in Tables 4–7 remain those of the original run. The statement in Section 4.3 that the smallest gaps are of the same order as run-to-run variation, which the repeated runs did not support, has been revised:

“To quantify run-to-run variation, the full LOSO protocol at 25 Hz was repeated with six training seeds (42–47), with the dataset and subject partitions unchanged, and the mixed model was refitted to each run.” (Section 2.11, page 13, lines 494–496)

“Across six repeated runs with different training seeds, the standard deviation of aggregate LOSO Macro F1 was 0.0005–0.0037 (Table 4 and Table S5), and refitting the mixed model to each run gave the same result: no pairwise contrast among Models A, B, D, and E reached significance (Tukey-adjusted p ≥ 0.89), and Model F was below every other model (p ≤ 0.001).” (Section 3.1, pages 13–14, lines 510–514)

“Six-run values are from repeated LOSO runs with training seeds 42–47 (Table S5); all other values are from the original run.” (Table 4, page 14, lines 539–540)

“Across six repeated runs with different training seeds, aggregate Macro F1 varied with a standard deviation of 0.0005–0.0037, and Model B was below Model A in every run (mean difference 0.0054). Small differences of this kind are therefore reproducible for these 15 animals, but they are far smaller than the subject-level confidence intervals and do not indicate which model would perform better on new animals. The ranking by aggregate Macro F1 (Model D first in all six runs) and by per-subject mean (Model A first in five of six) differed, but by margins well within these confidence intervals.” (Section 4.3, page 21, lines 767–774)

Comments 3: Section 4.2 hypothesizes that MSE‑based autoencoder (Model F) prioritizes high‑amplitude eating signals and ignores small‑amplitude rumination chewing pulses, leading to degraded classification performance. This mechanistic explanation is purely post‑hoc speculation without supporting experiments. Authors are encouraged to provide feature visualization (comparing activation patterns of supervised Model E vs unsupervised Model F for eating / rumination / other samples).

Response 3: Thank you. We agree that the mechanism was not supported by an experiment. A visualization of the learned representations would show how well the classes separate, which the per-class F1 values in Table 5 already quantify, but it would not test why; a direct test would require comparing the reconstruction error across signal components, which is beyond this revision. We have therefore shortened the explanation to a single sentence stated as an untested hypothesis, and the paragraph now leads with the observed class-dependent deficit:

“The deficit was strongly class-dependent, smallest for Eating (0.040 under LOSO), intermediate for Rumination (0.123), and largest for Other (0.218), consistent with the class-difficulty ordering. Model F nonetheless remained well above the chance level of 0.333, so the reconstruction objective yielded an informative but less discriminative representation. One possible explanation, not tested here, is that a mean-squared reconstruction objective favors high-amplitude signal components, such as the head movements of eating, over the small-amplitude chewing pulses that separate rumination from other low-motion states [37]. Its performance should be read as a limitation of the specific reconstruction objective tested here, not as evidence against label-free representation learning in general [38-40].” (Section 4.2, page 20, lines 720–725)

We hope that the revised manuscript addresses your concerns, and we thank you again for your time and helpful comments.

Sincerely,

Na-Yeon Kim, on behalf of all authors

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

No further comments

Comments on the Quality of English Language

Author Response

Thank you very much for your time and helpful comments in the previous round.

Reviewer 3 Report

Comments and Suggestions for Authors

The authors adequately addressed all my comments, reviewed the entire manuscript, and significantly improved its quality and clarity. I support the publication of this manuscript with the proposed edits.

Author Response

Thank you very much for your careful review and positive assessment, which have substantially improved the manuscript.

Review Reports

Response to Reviewer 1 Comments

1. Summary

2. Corrections identified by the authors

3. Point-by-point response to Comments and Suggestions for Authors

Response to Reviewer 2 Comments

1. Summary

2. Corrections identified by the authors

3. Point-by-point response to Comments and Suggestions for Authors

Response to Reviewer 3 Comments

1. Summary

2. Corrections identified by the authors

3. Point-by-point response to Comments and Suggestions for Authors

3.1 General comments

3.2 Comments in the annotated manuscript

Response to Reviewer 1 Comments

1. Summary

2. Correction identified by the authors

3. Point-by-point response to Comments and Suggestions for Authors