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A Three-Axis Stress Test of LLM vs Classical ML for Network Intrusion Detection under Distribution Shift and Adversarial Evasion

Muhammad Ebad Atif, Muhammad Haider Ali

Year: 2026Venue: arXiv preprintArea: cs.LGType: PreprintEmbeddings: 60

Intelligence

Status: succeeded | Model: Gemma-4-26B-A4B | Prompt: intel-v1 | Confidence: 92%

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Summary

This paper evaluates the robustness of Large Language Models (RoBERTa-LoRA) versus classical machine learning (XGBoost) for Network Intrusion Detection Systems (NIDS) across three axes: same-dataset performance, cross-dataset transfer under distribution shift, and adversarial evasion. Using two NetFlow v2 datasets (NF-UNSW-NB15-v2 and NF-CSE-CIC-IDS2018-v2), the study finds no universal winner: models are tied on same-dataset accuracy, XGBoost significantly outperforms RoBERTa-LoRA in cross-dataset transfer, and RoBERTa-LoRA excels in adversarial evasion. The research highlights that evaluation protocols relying solely on same-dataset accuracy are insufficient and argues for multi-axis robustness testing.

Entities (9)

RoBERTa-LoRA · machine-learning-model · 100%XGBoost · machine-learning-model · 100%NF-CSE-CIC-IDS2018-v2 · dataset · 95%NF-UNSW-NB15-v2 · dataset · 95%Adversarial evasion · evaluation-metricaxis · 90%Cross-dataset transfer · evaluation-metricaxis · 90%F1 Score · metric · 90%False Positive Rate · metric · 90%Network Intrusion Detection Systems · application-domain · 90%

Relation Signals (5)

XGBoost → outperforms → RoBERTa-LoRA

confidence 95% · XGBoost wins decisively under cross-dataset distribution shift, by 15 points of F1 and 25 points of balanced accuracy

RoBERTa-LoRA → outperforms → XGBoost

confidence 95% · RoBERTa-LoRA wins decisively under adversarial evasion, by roughly 17 points of F1

RoBERTa-LoRA → hashighfalsepositiverateunder → Cross-dataset transfer

confidence 90% · on the target network RoBERTa-LoRA's false positive rate reaches 0.78, leaving it barely above chance

NF-UNSW-NB15-v2 → usedinevaluationwith → NF-CSE-CIC-IDS2018-v2

confidence 90% · Evaluating XGBoost and RoBERTa-LoRA on two independently collected NetFlow v2 networks

Same-dataset evaluation → isinsufficientfor → Network Intrusion Detection Systems

confidence 85% · almost always using same-dataset evaluation, and that protocol turns out to be incomplete

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Abstract

Abstract:Large language models are increasingly benchmarked against classical machine learning for network intrusion detection (NIDS), almost always using same-dataset evaluation, and that protocol turns out to be incomplete. Evaluating XGBoost and RoBERTa-LoRA on two independently collected NetFlow v2 networks across three axes (same-dataset performance, cross-dataset transfer, and adversarial evasion) reveals no universal winner. The two models are statistically tied same-dataset. XGBoost wins decisively under cross-dataset distribution shift, by 15 points of F1 and 25 points of balanced accuracy; on the target network RoBERTa-LoRA's false positive rate reaches 0.78, leaving it barely above chance despite a superficially moderate F1. RoBERTa-LoRA wins decisively under adversarial evasion, by roughly 17 points of F1 at a representative mid-range perturbation strength, while both models hold false positive rates below 0.01 throughout. The model an evaluator would recommend therefore depends entirely on which axis is tested, not on same-dataset accuracy alone. A staged feature-leakage ablation improves cross-dataset transfer non-monotonically, indicating the leakage signal is distributed across the feature representation rather than confined to a few columns, and cross-dataset transfer between our two networks is strongly directional. These results argue for evaluating NIDS models along multiple independent robustness axes, and with more than one metric per axis.

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A Three-Axis Stress Test of LLM vs Classical ML for Network Intrusion Detection under Distribution Shift and Adversarial Evasion Muhammad Ebad Atif Affiliation: Dhanani School of Science and Engineering Habib University Karachi, Pakistan ma09639@st.habib.edu.pk Muhammad Haider Ali Affiliation: Faculty of Computer Sciences and Engineering Ghulam Ishaq Khan Institute of Engineering Sciences Swabi , Pakistan u2024385@giki.edu.pk Abstract Large language models are increasingly benchmarked against classical machine learning for network intrusion detection (NIDS), almost always using same-dataset evaluation, and that protocol turns out to be incomplete. Evaluating XGBoost and RoBERTa-LoRA on two independently collected NetFlow v2 networks across three axes (same-dataset performance, cross-dataset transfer, and adversarial evasion) reveals no universal winner. The two models are statistically tied same-dataset. XGBoost wins decisively under cross-dataset distribution shift, by 15 points of F1 and 25 points of balanced accuracy; on the target network RoBERTa-LoRA’s false positive rate reaches 0.78, leaving it barely above chance despite a superficially moderate F1. RoBERTa-LoRA wins decisively under adversarial evasion, by roughly 17 points of F1 at a representative mid-range perturbation strength, while both models hold false positive rates below 0.01 throughout. The model an evaluator would recommend therefore depends entirely on which axis is tested, not on same-dataset accuracy alone. A staged feature-leakage ablation improves cross-dataset transfer non-monotonically, indicating the leakage signal is distributed across the feature representation rather than confined to a few columns, and cross-dataset transfer between our two networks is strongly directional. These results argue for evaluating NIDS models along multiple independent robustness axes, and with more than one metric per axis. Index Terms: machine learning, cybersecurity, network intrusion detection, large language models, adversarial evasion, distribution shift, cross-dataset generalization, robustness evaluation. 00footnotetext: Code and reproduction materials: https://github.com/ebadatif/IDS-three-axis-evaluation I Introduction Machine learning-based Network Intrusion Detection Systems (NIDSs) are increasingly benchmarked against large language models, typically using a same-dataset protocol: train and test on splits from a single network. This is convenient, but it says little about two conditions that matter in practice: deployment on a different network and an adversary deliberately crafting evasive traffic. Same-dataset evaluation exercises neither. The risk of overstating what such an evaluation demonstrates for real-world NIDS deployment is a long-standing concern, dating back to Sommer and Paxson [1]’s critique of closed-world evaluation in ML-based intrusion detection. Recent surveys catalogue the temporal leakage, weak splitting protocols, and poor cross-dataset generalization that inflate reported NIDS results [2]. Recent work moves past same-dataset evaluation, but only one axis at a time. Mehavilla et al. [3] compare LLMs and classical models same-dataset, finding XGBoost wins accuracy while LLMs are more data-efficient. Bui/Boffa et al. [4] test generalization within a single network via a time-based, zero-day split, finding fine-tuned BERT beats classical ML in-distribution but degrades sharply under attack drift. Neither evaluates cross-dataset transfer between independently collected networks, nor adversarial evasion. Bui/Boffa themselves flag zero-day generalization within their own dataset as the most urgent open direction, leaving the two axes we examine outside their reported scope. This gap matters because, as we show, these two axes can yield opposite conclusions about which model is preferable; a verdict from either alone risks being incomplete. This paper evaluates XGBoost and RoBERTa-LoRA across both axes, on two independently collected NetFlow v2 networks, under one shared harness. No model wins universally: the two are statistically tied same-dataset, XGBoost wins decisively under cross-dataset shift, and RoBERTa-LoRA wins decisively under adversarial evasion by roughly 17 F1 points at a representative mid-range perturbation strength. Which model an evaluator would recommend therefore depends on which axis they choose to test. A secondary methodological finding runs through both axes: F1 alone is insufficient to characterize either result, since on the cross-dataset axis it conceals a near-chance classifier behind a moderate score, while on the adversarial axis only the false positive rate distinguishes robustness from indiscriminate flagging. Two additional findings arose as the work progressed. A staged feature-ablation study shows that leakage removal does not improve cross-dataset transfer monotonically, indicating the leakage signal is distributed rather than confined to a few columns. Cross-dataset transfer between our two networks is also strongly directional, a pattern related to differing attack character across networks, though this mechanism was not directly verified (Sec. V). Sec. I positions this work against prior LLM-NIDS studies. Sec. I-A–I-F cover datasets, ablation, models, and evaluation protocol. Sec. IV-D reports results across all three axes. Sec. V argues the paper’s thesis and explains the ablation and transfer findings. Sec. VI states scope constraints, and Sec. VII closes the paper. I Related Work Whether large language models are competitive with classical machine learning for network intrusion detection is a growing question, but existing studies each stress-test only one axis of robustness at a time. This section positions the present work against the two most directly comparable studies. Same-dataset comparison: Mehavilla et al. Mehavilla et al. [3] evaluate LLMs directly as flow classifiers, comparing small decoder-only transformers (GPT-2, GPT-Neo-125M, LLaMA-3.2-1B) against classical machine learning (Random Forest, XGBoost) and deep learning baselines (MLP, GRU, LeNet-5) on the CIC-IoT-2023 dataset. Their evaluation is entirely same-dataset: models are trained and tested on splits drawn from the same underlying traffic distribution. XGBoost wins on accuracy (F1 ≈ 0.97 on their multiclass task), narrowly ahead of the best fine-tuned LLM (≈ 0.96). Their one clear LLM advantage is data efficiency: pre-trained LLMs are already near their performance ceiling with 10,000 samples per class, while the deep learning baselines need substantially more data to reach comparable performance. Their study does not evaluate cross-dataset transfer or adversarial robustness – a limitation the authors themselves note, alongside their use of only three small LLMs and single-run (non-multi-seed) results. Distribution shift: Bui/Boffa et al. Bui/Boffa et al. (CoNEXT 2024) [4] take a complementary angle, comparing fine-tuned BERT against a large classical ML sweep (over 50 model/hyperparameter combinations) under both a standard stratified split and a time-based, zero-day split (their 15/08-split) designed to test generalization to novel attacks. In-distribution, their fine-tuned BERT consistently beats the best classical model, by a mean pairwise difference of 5 percentage points of weighted accuracy (95% CI [0.04, 0.06]). Under their zero-day split, performance degrades sharply for every model. BERT falls from 98% to 79% weighted accuracy in their most information-rich IDS-assistance configuration (payload + 5-tuple + eventName inputs), and the drop is comparable in less-favourable configurations (e.g. 88% to 73% for the IDS-replacement setting with payload + 5-tuple). They further find that scaling to a larger LLM (Mistral-7B) provides no measurable benefit over the much smaller BERT-base (−0.0%-0.0\% relative to the BERT baseline in their ablation). Domain-specific pretraining (SecureBERT, UniXcoder) yields only marginal gains (+0.7%+0.7\% and +1.1%+1.1\% respectively), and they conclude that a small, well-fine-tuned model is the practical sweet spot. Like Mehavilla et al., their study does not include an adversarial evasion axis, and the authors flag zero-day generalization within their dataset as the most urgent open direction, not cross-dataset transfer between independently collected networks. Between these two studies, three evaluation axes for LLM-vs-classical NIDS comparison have each been examined once: same-dataset accuracy (Mehavilla et al.), zero-day/temporal generalization within a single network (Bui/Boffa et al.), and, separately, general-purpose prompting and RAG-based approaches with frozen LLMs (also evaluated by Bui/Boffa et al., and found to substantially underperform fine-tuning). Neither study, nor, to our knowledge, any other work in this space, evaluates cross-dataset transfer between two independently collected networks and adversarial evasion robustness on the same pair of matched models. This gap matters because these two axes, as Sec. V shows, can produce opposite rankings between the same two models: a comparison run on only one of them risks generalizing a conclusion (“XGBoost beats RoBERTa” or “RoBERTa beats XGBoost”) that does not hold under the other. The present study addresses this by evaluating XGBoost and RoBERTa-LoRA under a single, shared harness across same-dataset, bidirectional cross-dataset transfer, and adversarial evasion, on the same NetFlow v2 feature schema throughout. The cross-dataset finding reported here (Sec. IV-B), near-perfect same-dataset performance that collapses under distribution shift, is not an isolated result. Cantone et al. [5] independently document the same pattern using four classifiers across four NIDS datasets, and their work is, to our knowledge, the closest existing confirmation of the effect measured here between NF-UNSW-NB15-v2 and NF-CSE-CIC-IDS2018-v2. Related work reports similar generalization failure in adjacent settings, including enterprise datasets [6], IIoT network deployments, and unsupervised NIDS models. Several of these call for standardized cross-evaluation frameworks and explainability-driven analysis of what fails to transfer and why. Separately, a recent comparison of tabular representation learning against transformer baselines for NIDS finds no single approach consistently dominates across evaluation scenarios [7], a parallel to the “no universal winner” finding of Sec. V obtained along a different pair of evaluation axes. I Methodology The experimental design follows the methodological pitfalls catalogued by Arp et al. [8] for machine learning in computer security: avoiding data snooping between train and test splits (Sec. I-B), auditing for spurious, non-causal features before reporting results (Sec. I-C), and evaluating with a realistic, deployment-relevant protocol rather than same-dataset accuracy alone (Sec. I-F). I-A Datasets We use two datasets from the University of Queensland NetFlow v2 collection: NF-UNSW-NB15-v2 and NF-CSE-CIC-IDS2018-v2 [9]. Both are re-extracted from the original raw PCAP captures of UNSW-NB15 and CSE-CIC-IDS2018 into an identical, standardized schema of 43 NetFlow features, in the same column order. That shared schema makes a fair cross-dataset comparison possible. Without it, any transfer result would be confounded by differing feature definitions rather than reflecting a distribution shift between networks. NF-UNSW-NB15-v2 contains approximately 2.39M flows, of which 3.98% are attack traffic. NF-CSE-CIC-IDS2018-v2 is substantially larger, at approximately 18.9M flows, with 11.95% attack traffic, roughly a threefold difference in attack prevalence (addressed in Sec. I-B via balanced sampling). The two datasets originate from different institutions, years, and network configurations. UNSW-NB15 was generated at the Australian Centre for Cyber Security (UNSW Canberra), while CSE-CIC-IDS2018 was generated by the Canadian Institute for Cybersecurity. That institutional and temporal separation makes the pair a valid basis for testing cross-dataset generalization, as opposed to evaluating on a held-out split of the same collection process. Attack taxonomy mismatch. The two datasets’ attack categories are almost entirely disjoint. UNSW-NB15 attacks are labeled as Exploits, Fuzzers, Reconnaissance, Generic, DoS, Shellcode, Backdoor, Analysis, and Worms. CSE-CIC-IDS2018 attacks are labeled as DDoS variants (HOIC, LOIC-HTTP, LOIC-UDP), DoS variants (Hulk, GoldenEye, Slowloris, SlowHTTPTest), Infiltration, Bot, Brute Force (SSH, FTP, Web, XSS), and SQL Injection. Only the coarse category “DoS” overlaps even loosely between the two label sets. Because the label spaces are effectively disjoint, multiclass cross-dataset evaluation is not meaningful: a model cannot be evaluated on attack subtypes it never saw during training. The task is therefore collapsed to binary classification (benign vs. attack) for all cross-dataset experiments, the only label granularity shared by both datasets. The pipeline consequently records only the aggregate binary confusion matrix in every condition, which constrains the mechanistic analysis in Sec. V. Before any modeling was performed, identically named columns in the two datasets turned out to be stored with different data types. IN_PKTS is stored as int16 in NF-UNSW-NB15-v2 but int32 in NF-CSE-CIC-IDS2018-v2, and SRC_TO_DST_SECOND_BYTES is float32 versus float64. Since each dataset’s original storage type was chosen to fit its own value range, this divergence is itself evidence of a real distributional difference: CSE-CIC-IDS2018 contains flows with packet and byte counts that exceed the range representable by UNSW-NB15’s narrower types. This is treated as an independent, pre-modeling signal that the cross-dataset shift measured later on is real and not an artifact of the pipeline. I-B Preprocessing Balanced sampling. Attack prevalence differs roughly threefold between the two datasets (Sec. I-A). Because precision and recall are both sensitive to base rate, evaluating models across datasets with different prevalence would confound two distinct effects: a shift in the underlying traffic distribution, and a shift in how often the positive class occurs. To isolate the former, balanced subsets are drawn from both datasets (50,000 flows per class) so that attack prevalence is identical in every training and test split. Any drop in cross-dataset performance reported in Sec. IV-B can therefore be attributed to distribution shift, not to a difference in class balance between source and target. This mirrors the balanced-sampling approach used by Mehavilla et al. [3]. The balanced protocol places attack prevalence far above any realistic operational base rate, so absolute precision figures throughout this paper should be read as comparative between models rather than as deployment estimates. This is why false positive rate is reported alongside precision. The dtype divergence noted above is informative as evidence of distribution shift, but it is also a practical obstacle: models cannot be trained on features that are not uniformly typed across datasets. Non-finite and extreme values are capped at the 99.9th percentile of each feature, computed from the UNSW (training) side only to avoid test-set leakage, and the same caps are applied to CIC. Every feature is then cast to float32 at load time, so that both datasets present an identical, bounded numeric schema to every downstream model. Before any leakage-driven feature ablation (Sec. I-C), four columns are dropped outright: L4_SRC_PORT, L4_DST_PORT, DNS_QUERY_ID, and the multiclass Attack label (retained separately for post-hoc analysis only, never as a feature). The three non-label columns are session identifiers. A source or destination port number, or a DNS query ID, describes which specific connection a flow belongs to, saying nothing about what that connection did. Retaining them would risk the model memorizing connection identity instead of learning transferable attack behavior, the failure mode the rest of the feature analysis is designed to guard against. The task is framed as binary classification. The Label column (benign vs. attack) is the prediction target; the Attack column, which encodes the fine-grained multiclass attack subtype, is dropped from the feature set entirely. As established in Sec. I-A, this binary framing is a requirement of the disjoint label spaces, so no multiclass target could be shared between the two datasets. Random seeds (42–45) are built into the data loading and model training pipeline from the start. Every classical model result in this paper is obtained by re-running the full pipeline, sampling through training to evaluation, under each of the four seeds independently. This was a deliberate design decision: multi-seed evaluation is straightforward to build in from the outset and difficult to retrofit cleanly, particularly once balanced sampling introduces its own source of randomness. I-C Feature Ablation Study Time-to-live (TTL) is a counter set by the sending operating system at a fixed default (commonly 64 for Linux/Mac, 128 for Windows, or 255 for some network hardware) and decremented by one at each network hop. The value observed at the receiving end therefore encodes which operating system sent the packet and how many hops away it originated – information about the network’s physical and software topology, and nothing about the content or intent of the traffic. In NF-UNSW-NB15-v2, benign and attack traffic were generated by different machines during dataset construction. A model can consequently learn a rule of the form “TTL = X implies benign, TTL = Y implies attack” that is entirely accurate on this dataset while reflecting nothing about attack behavior: it has memorized which machine generated a flow. This single, concrete leakage mechanism motivated a systematic search for other features exhibiting the same problem. To flag ablation candidates, each feature’s solo predictive power against the label is computed using a one-level decision stump (a single-feature threshold split) fit on that feature alone and scored on held-out data. A high score marks a feature for investigation; solo F1 >0.90>0.90 is used as the flag threshold, and a flag triggers scrutiny rather than automatic removal. The audit was run iteratively, re-computed after each round of removals, to check whether remaining features still stood in for the label on their own. Two other diagnostics accompanied the solo-F1 stump: full-model F1 on the candidate feature set, to catch collapse before it reached cross-dataset testing, and XGBoost’s built-in feature-importance ranking, to check whether the model leaned on one or two features disproportionately. Applying this audit to the full 38-feature set surfaced three groups of suspects, grouped by the source and pattern of their solo predictive power. The first is TTL (MIN_TTL, MAX_TTL), flagged via the mechanism described above. The second is the packet-length features (MIN_IP_PKT_LEN, MAX_IP_PKT_LEN, SHORTEST_FLOW_PKT, LONGEST_FLOW_PKT), fixed per-flow size statistics that can reflect equipment or capture configuration as easily as behavior. The third is a smaller group of remaining high-solo-F1 features (SERVER_TCP_FLAGS, TCP_WIN_MAX_IN, TCP_WIN_MAX_OUT). For none of these three groups could an environmental fingerprint be cleanly separated from discriminative behavior using solo F1 alone – a feature can score highly for either reason, and the stump test does not distinguish them. The three groups were therefore treated as three competing hypotheses about where the leakage boundary sits, resolved empirically by testing each group’s removal against cross-dataset transfer (Sec. IV-B). Cross-dataset F1, not same-dataset solo F1, is the arbiter of whether a suspected feature was leaking. Corresponding to the three suspect groups above, three progressively larger removals were evaluated, each scored on both same-dataset and cross-dataset performance: • Set A (36 features): drop TTL only. • Set B (32 features): drop TTL and packet-length features. • Set C (29 features): an aggressive drop, additionally removing SERVER_TCP_FLAGS, TCP_WIN_MAX_IN, and TCP_WIN_MAX_OUT. Staging the removals shows how transfer performance responds at each step. All three sets are evaluated under an identical protocol, train on the full source dataset and test on the full target dataset, matching the cross-dataset harness of Sec. I-F, so that ablation results and benchmark results are directly comparable. Table I shows that the ablation did not improve cross-dataset transfer monotonically. Set A left cross-dataset F1 low (0.0488, FNR 0.9656). Set B made transfer worse, dropping cross-dataset F1 to 0.0282 with a false-negative rate of 0.9851, despite removing more candidate leakage features than Set A. Only Set C recovered cross-dataset performance (F1 0.8116, FNR 0.1293). Throughout all three sets, same-dataset F1 barely moved: 0.9972 in Sets A and B, 0.9966 in Set C, a difference of six ten-thousandths. Because same-dataset performance is insensitive to which leakage features are present, the leakage signal cannot be isolated to one or two columns – it is distributed across the feature representation. Removing part of it (Set B) can disturb a competing, transferable signal while leaving enough leakage-adjacent structure intact to mislead the model on the target domain. Set C (29 features) is locked as the final feature schema. Every cross-dataset and adversarial-evasion result reported in this paper (Sec. IV-B, Sec. IV-C) uses Set C exclusively; same-dataset results in Table I are also reported under Set C for consistency across all conditions. I-D Models The primary classical model is XGBoost, trained with 100 trees, n_jobs=-1, and eval_metric=logloss. Every XGBoost result reported in this paper is obtained across four seeds (42–45), using the locked Set C feature schema. Random Forest is used as a secondary classical baseline, trained under the same seed set and feature schema, to check whether findings attributed to XGBoost are specific to gradient boosting or hold across tree-based methods generally. The LLM model is RoBERTa-base, fine-tuned with LoRA adapters, using rank r=8r=8, scaling factor α=16α=16, with adapters applied to the query, key, and value projection matrices, leaving approximately 0.82% of total model parameters trainable. Each of the two LLM arms (UNSW-trained and CIC-trained) is fine-tuned in a single run from a freshly loaded pretrained checkpoint with a freshly initialised adapter, so neither arm carries optimization history from the other or from any earlier run. This is stated explicitly because prior work [3] found that fine-tuning from pretrained weights versus training from scratch materially affects downstream performance. RoBERTa operates on text, so each flow record is serialized into a string prior to tokenization. Every feature in the Set C schema is rendered as a FEATURE=value pair, and these pairs are concatenated into a single string representing one flow. This step is specific to the LLM arm; XGBoost and Random Forest consume the same Set C features directly as numeric vectors, with no text conversion. Serializing feature names into the input text gives RoBERTa an explicit structural signal, the identity of each feature, that the numeric-only classical models do not receive. XGBoost and Random Forest see only feature values, positioned by column order, with no access to feature names at inference time. The two arms therefore do not operate on strictly identical information, and any performance comparison between them (Sec. IV-A–IV-C) should be read with this asymmetry in mind. Sec. V returns to it as the leading candidate explanation for RoBERTa-LoRA’s comparative stability under adversarial evasion. Unlike the four-seed classical arm, RoBERTa is trained with a single seed per condition, due to the compute cost of LoRA fine-tuning across every condition in the study. RoBERTa results are therefore reported as point estimates rather than mean ± std throughout; Sec. VI revisits the implications. I-E Adversarial Evasion Attack Robustness to adversarial evasion is evaluated using a feature-space “drift toward benign” attack. Let x denote the perturbable-feature vector of an attack flow (the perturbable subset is defined below), and let μ denote the centroid of benign flows in that same feature space, =1|ℬ|∑∈ℬ, μ= 1|B| _b b, (1) computed over the benign flows ℬB in the training split only, so that the attacker is not given access to held-out data. For a perturbation strength ε∈[0,1] ∈[0,1], the perturbed flow is generated by linear interpolation toward this centroid, ′(ε)=(1−ε)+ε,x ( )=(1- )\,x+ \, μ, (2) followed by projection through the domain-constraint operator Π⁡(⋅) (·) described below, giving the final perturbed flow Π(′(ε)) (x ( )). Ten perturbation strengths are swept, where ε=0 =0 reproduces the original attack flow (′(0)=x (0)=x) and ε=1 =1 moves the flow fully to the benign centroid (′(1)=x (1)= μ). Constrained feature-space perturbation of this kind is an established methodology for approximating realistic evasion without requiring a full problem-space attack implementation [10], and the same rationale is adopted here. Naive linear interpolation over raw feature values can produce flows that are not physically realizable, such as negative byte counts or fractional packet counts. To keep perturbed flows within a plausible feature space, the projection operator Π⁡(⋅) (·) in Eq. (2) enforces four constraints: non-negativity of all features, integer-valued packet and byte counts, retransmitted-byte counts bounded above by total byte counts, and fixed categorical features (protocol, L7 protocol, ICMP type, DNS query type, FTP return code) left unperturbed, i.e. Π(′)j=xj (x )_j=x_j for those coordinates regardless of ε . Of the 29 Set C features, 23 are perturbable under this scheme (the coordinates of x in Eq. (2)) and 6 are held fixed. These constraints do not guarantee that a perturbed flow is realizable by an actual attacker in the underlying network protocol (see Sec. VI), but they rule out perturbations that are trivially infeasible. At every ε , the evaluation set holds the 15,000 perturbed attack flows from the UNSW held-out split together with the 15,000 untouched benign flows from that same split. Only the attacker’s own traffic is perturbed; normal traffic is left unmodified, as it would be in a real deployment. Including benign traffic is essential: an attacks-only evaluation set makes precision trivially unity by construction and renders false positives unmeasurable. A model that simply labels everything an attack would therefore appear maximally robust. F1, precision, recall and false positive rate are therefore reported at every ε , with the FPR column serving as the check on whether a high recall reflects robustness or indiscriminate flagging. By Eq. (2), ′(1)=x (1)= μ regardless of the original flow x: the interpolation target is a single point, the benign centroid, so as ε→1 → 1 every perturbed attack flow converges to the same location in perturbable-feature space. This is quantified by counting distinct perturbed attack rows at each ε : the count is stable at 8,350 for every ε≤0.5 ≤ 0.5, falls to 8,349 at ε=0.7 =0.7, and collapses to 1 at ε=1.0 =1.0. The ε=1.0 =1.0 condition therefore does not measure robustness over 15,000 independent trials; it reports one model decision replicated 15,000 times, with an effective sample size of one. It is reported for completeness but excluded from Fig. 4, and no claim is based on it; ε≤0.7 ≤ 0.7 is treated as the valid measurement range. The adversarial evasion attack is evaluated same-dataset only, on NF-UNSW-NB15-v2, using the locked Set C feature schema. Adversarial evasion is not evaluated under cross-dataset transfer; the two stress axes are examined independently in this study. I-F Evaluation Protocol Every model and every condition in this paper – same-dataset, cross-dataset in both directions, and adversarial evasion at all ten ε values – is scored using one shared evaluation function computing F1, precision, recall, balanced accuracy, false positive rate (FPR), false negative rate (FNR), and throughput (flows/sec). A single harness across the classical and LLM arms guarantees that any performance difference reported in Sec. IV-A–IV-C reflects the models themselves and not differences in scoring. As one consistency check, the ε=0 =0 row of the adversarial sweep reproduces the same-dataset UNSW confusion matrix exactly for both models, confirming that the two blocks evaluate the identical baseline. The harness is applied under three conditions, which together define the three axes of this study: a same-dataset condition, training on a 70% split and testing on the held-out 30% of the same network; a cross-dataset condition, training on the full source network and testing on the full target network in both directions; and an adversarial evasion condition, testing same-dataset performance against the perturbed attack flows described in Sec. I-E. Sec. IV-D reports results for all three conditions and every model. IV Results All results use the locked Set C feature schema (29 features) unless otherwise noted. XGBoost and Random Forest are evaluated across four seeds (42–45); RoBERTa-LoRA reflects a single training run per condition due to compute cost (Sec. VI), so RoBERTa figures are point estimates rather than mean ± std. IV-A Same-Dataset Performance Table I reports in-distribution performance: train and test on the same network. Both models are effectively tied. XGBoost reaches 0.9960–0.9971 F1 on UNSW-NB15 and 0.9764–0.9783 on CIC-IDS2018 across the four seeds; RoBERTa-LoRA reaches 0.9938 and 0.9745 respectively. The gap never exceeds 0.004 F1 in either direction. TABLE I: Same-dataset F1 (XGBoost: mean over 4 seeds, RoBERTa: single seed) Dataset XGBoost RoBERTa-LoRA Gap UNSW-NB15 0.9966 0.9938 +0.0028 CIC-IDS2018 0.9776 0.9745 +0.0031 This is the number the field typically reports, and, as the following two subsections show, it is also the least informative number for predicting deployment behavior. Beyond accuracy, the two arms differ sharply in inference throughput (Fig. 1). XGBoost processes on the order of 10610^6 flows/sec versus RoBERTa-LoRA’s ∼ 10210^2, an ∼ 5,806× difference that bears directly on line-rate deployment even though same-dataset accuracy is near-identical. RoBERTa-LoRA throughput is measured end-to-end, including per-flow text serialization and tokenization, both required in deployment; XGBoost throughput reflects native numeric prediction on already-vectorized input. The comparison is between complete inference pipelines, not model forward passes alone. Fig. 1: Near-identical same-dataset F1 at vastly different inference throughput (log scale). XGBoost processes roughly four orders of magnitude more flows per second than RoBERTa-LoRA. IV-B Cross-Dataset Transfer IV-B1 Feature ablation is non-monotonic Table I shows the effect of progressively removing candidate leakage features on XGBoost, evaluated both in-distribution (SD) and under cross-dataset transfer (CD, UNSW→ ). TABLE I: Feature ablation: same-dataset vs. cross-dataset F1 (XGBoost, UNSW→ ) Feature set #Feat SD F1 CD F1 CD FNR A: drop TTL only 36 0.9972 0.0488 0.9656 B: drop TTL + pkt. len. 32 0.9972 0.0282 0.9851 C: aggressive drop 29 0.9966 0.8116 0.1293 Fig. 2: Same-dataset F1 (grey) is flat across all three ablation sets while cross-dataset F1 (blue) swings non-monotonically, recovering only at Set C. Same-dataset accuracy cannot reveal which features leak. Removing leakage features does not improve cross-dataset transfer monotonically. Set B, which drops more features than Set A, performs worse on cross-dataset F1 (0.0282 vs. 0.0488) and carries a false-negative rate of 0.9851, missing nearly every attack in the target domain. Only the aggressive Set C recovers transfer performance (0.8116 F1, FNR 0.1293), while same-dataset F1 stays essentially flat across all three sets (0.9966–0.9972). The leakage signal is therefore not concentrated in the TTL and packet-length features but distributed across the feature representation. Partial removal can strip a competing, transferable signal while leaving enough leakage-adjacent structure intact to mislead the model on the target domain. IV-B2 Transfer is asymmetric under the locked feature set Using Set C, Table I reports both transfer directions for all three models, and Fig. 3 shows the full matrix. TABLE I: Cross-dataset F1 under Set C (29 features) Direction XGBoost Random Forest RoBERTa-LoRA UNSW → CIC 0.8116 0.5662–0.7587 0.6582 CIC → UNSW 0.0730 0.0201–0.0378 0.0599 Fig. 3: Cross-dataset transfer across both directions, for both models. On-diagonal (same-dataset) cells are near-perfect; the off-diagonal CIC→ cell collapses for both models, while UNSW→ remains workable for XGBoost. The asymmetry is architecture-independent. XGBoost beats RoBERTa-LoRA by 15.3 points of F1 in the forward direction (0.8116 vs. 0.6582), and the F1 column understates the gap: Table IV decomposes it. TABLE IV: Cross-dataset UNSW→ , decomposed. F1 conceals a near-chance classifier. Metric XGBoost RoBERTa-LoRA Random Forest F1 0.8116 0.6582 0.5662–0.7587 Precision 0.7601 0.5290 0.5546–0.6932 Recall 0.8707 0.8709 0.5783–0.8380 FPR 0.2748 0.7756 0.3710–0.4852 Balanced accuracy 0.7979 0.5477 0.5569–0.7335 The two models achieve statistically indistinguishable recall on the target network (0.8707 vs. 0.8709). The entire F1 gap comes from precision, and the FPR row shows why: RoBERTa-LoRA labels 38,780 of 50,000 benign CIC flows as attacks, a false positive rate of 0.7756. Its balanced accuracy on the target network is 0.5477, barely above chance, against XGBoost’s 0.7979. Read through balanced accuracy, RoBERTa-LoRA’s cross-dataset transfer is close to non-functional: it retains sensitivity to attacks only by flagging most normal traffic as well. Random Forest sits between the two on every metric. XGBoost shows zero variance across seeds in cross-dataset conditions (std = 0.000, Table V), while Random Forest varies substantially (std 0.0830, range 0.5662–0.7587 UNSW→ ). This gap in variance is a direct consequence of how each model is evaluated. The cross-dataset evaluation uses the full target dataset for testing with no train/test split randomness, so XGBoost with fixed hyperparameters produces deterministic predictions on a fixed 100k-row test set. Random Forest’s variance, by contrast, comes from bagging randomness in tree construction, which XGBoost’s sequential boosting does not have in the same form. TABLE V: Seed variance, cross-dataset UNSW→ (seeds 42–45) Model F1 range Std XGBoost 0.8116 – 0.8116 0.0000 Random Forest 0.5662 – 0.7587 0.0830 The CIC→ direction collapses for every model (0.0201–0.0730 F1). Here balanced accuracy confirms the F1 reading rather than reinterpreting it: XGBoost reaches 0.5050 and RoBERTa-LoRA 0.5042, both indistinguishable from chance, with recall of 0.0390 and 0.0316 respectively. Both models fail by the opposite mechanism to the forward direction, predicting almost nothing as an attack. Sec. V discusses candidate mechanisms for the asymmetry. IV-C Adversarial Evasion Fig. 4 plots F1 and false positive rate against perturbation strength ε for XGBoost and RoBERTa-LoRA under the feature-space drift-to-benign attack (same-dataset, UNSW-NB15 only, 15,000 perturbed attacks plus 15,000 untouched benign flows). Table VI reports the full sweep. TABLE VI: Adversarial evasion by ε : F1 and FPR on a balanced eval set (15k perturbed attacks + 15k untouched benign) XGBoost RoBERTa-LoRA ε F1 FPR F1 FPR 0.00 0.9966 0.0057 0.9938 0.0081 0.05 0.9718 0.0057 0.9703 0.0081 0.10 0.9702 0.0057 0.9797 0.0081 0.15 0.6917 0.0057 0.9552 0.0081 0.20 0.6191 0.0057 0.9675 0.0081 0.30 0.7408 0.0057 0.9553 0.0081 0.40 0.8202 0.0057 0.8884 0.0081 0.50 0.7720 0.0057 0.9448 0.0081 0.70 0.6552 0.0057 0.9247 0.0081 Degenerate endpoint (1 distinct attack row): 1.00 0.0000 0.0057 0.9959 0.0081 Fig. 4: F1 vs. perturbation strength ε on the balanced evaluation set (15,000 perturbed attack flows plus 15,000 untouched benign flows). The degenerate ε=1.0 =1.0 endpoint is excluded. The first and most important observation is that neither model trades false positives for detection. FPR is 0.0057 for XGBoost and 0.0081 for RoBERTa-LoRA at every ε , because benign traffic is not perturbed. RoBERTa-LoRA’s sustained detection therefore reflects robustness rather than a tendency to label everything an attack. The same diagnostic, applied to the cross-dataset axis in Sec. IV-B, returned the opposite verdict for the same model. The two models also differ in the magnitude of degradation rather than its smoothness. Across the valid range (ε≤0.7 ≤ 0.7) RoBERTa-LoRA moves within a band of roughly 10 points, from 0.9938 at ε=0 =0 down to 0.8884 at ε=0.40 =0.40 and back to 0.9247 at ε=0.70 =0.70. XGBoost swings across roughly 38 points, from 0.9966 down to 0.6191 at ε=0.20 =0.20, back up to 0.8202 at ε=0.40 =0.40, and down again to 0.6552 at ε=0.70 =0.70. Both curves are non-monotonic; the contrast is one of amplitude. XGBoost’s precision never degrades, remaining between 0.9876 and 0.9944 across the entire sweep while recall falls from 0.9989 to 0.4509. RoBERTa-LoRA’s precision is likewise stable (0.9900–0.9919). Where the attack succeeds, it succeeds by pushing attack flows below the decision threshold, never by inducing false alarms on benign traffic. At the representative mid-range strength ε=0.5 =0.5, RoBERTa-LoRA leads XGBoost by 17.3 F1 points (0.9448 vs. 0.7720), and the gap reaches 34.8 points at ε=0.20 =0.20, where XGBoost is at its weakest. This axis reverses the Sec. IV-B ranking: RoBERTa-LoRA wins under adversarial evasion, having trailed XGBoost by 15.3 points under distribution shift. Random Forest is excluded from this comparison, as the adversarial evasion axis was evaluated for XGBoost and RoBERTa-LoRA only. IV-D Summary Across Axes Table VII collects all three axes for XGBoost and RoBERTa-LoRA, and Fig. 5 summarizes the reversal at a glance. Which model wins depends entirely on which axis is evaluated. No single benchmark number in that table characterizes deployment-relevant performance on its own. TABLE VII: Master results: F1 across all evaluation axes Condition XGBoost RoBERTa-LoRA Gap Same-dataset (UNSW) 0.9966 0.9938 +0.0028 Same-dataset (CIC) 0.9776 0.9745 +0.0031 Cross-dataset (UNSW→ ) 0.8116 0.6582 +0.1534 Cross-dataset (CIC→ ) 0.0730 0.0599 +0.0131 Adversarial (ε=0.2 =0.2) 0.6191 0.9675 −-0.3484 Adversarial (ε=0.5 =0.5) 0.7720 0.9448 −-0.1728 Adversarial (ε=0.7 =0.7) 0.6552 0.9247 −-0.2695 Fig. 5: The same two models produce three different verdicts. Same-dataset (both networks): statistically tied. Cross-dataset (UNSW→ ): XGBoost wins. Adversarial evasion (ε=0.5 =0.5): RoBERTa-LoRA wins. No single axis predicts the others. V Discussion XGBoost and RoBERTa-LoRA cannot be ranked on a single scale. Same-dataset, they are statistically indistinguishable (within 0.004 F1 on both datasets). Under cross-dataset transfer, XGBoost wins by roughly 15 F1 points UNSW→ and by 25 points of balanced accuracy, a gap that widens once the metric accounts for false positives. Under adversarial evasion, RoBERTa-LoRA wins by 17 to 35 F1 points depending on perturbation strength, at comparable and very low false positive rates. Each axis evaluated alone would support a confident but incomplete claim about which model is “better.” Model selection for NIDS deployment should therefore be driven by the anticipated threat model, not by same-dataset benchmark leaderboards. An operator primarily concerned with deploying across networks unlike their training data should prefer XGBoost; an operator primarily concerned with an adaptive adversary who can manipulate flow features should prefer RoBERTa-LoRA, inference budget permitting (Sec. IV-A). No evaluation axis in isolation answers the question a deployer actually has. A secondary finding cuts across two of the three axes. On the cross-dataset axis, RoBERTa-LoRA’s F1 of 0.6582 looks like degraded but functional transfer; its balanced accuracy of 0.5477 and FPR of 0.7756 show a classifier close to labelling everything an attack. On the adversarial axis, RoBERTa-LoRA’s sustained F1 could in principle have had the same explanation. An attacks-only evaluation protocol, common in this literature, could not have distinguished the two cases, because precision is unity by construction when the evaluation set contains no benign traffic. Only the FPR column, measurable because untouched benign flows are retained at every ε (Sec. I-E), separates robustness (0.0081, sustained) from the cross-dataset failure mode (0.7756). The same diagnostic returns opposite verdicts for the same model on two different axes, which is why adversarial NIDS evaluations should retain benign traffic in the evaluation set and report FPR alongside F1 as a matter of protocol. The three explanations that follow are hypotheses consistent with the data reported here, not verified mechanisms. Confirming any of them requires diagnostics the present pipeline does not currently produce: feature attribution (e.g. SHAP) for the ablation account, per-attack-subtype recall for the transfer asymmetry, and attention-weight inspection or serialization ablation for the evasion account. Sec. VI details what each would require. They are stated here because they are the leading candidates and because naming them makes them testable, not because the evidence settles them. The non-monotonic ablation result (Table I) is counterintuitive: removing more candidate leakage features (Set B) produces worse cross-dataset transfer than removing fewer (Set A), despite same-dataset F1 remaining unchanged across both. One interpretation is a competing-signal hypothesis. Packet-length features carry environment-correlated signal, but they also carry transferable behavioral information, such as coarse differences in flow size between benign and malicious traffic that hold across networks. Set A, which removes only TTL, retains this transferable component alongside the leakage. Set B removes the packet-length features entirely, discarding the transferable component along with whatever leakage it carried, and leaves the model with less signal to generalize on, hence the drop to 0.0282 F1 and a false-negative rate of 0.9851. Only in Set C, once the broader group of environment-correlated features is removed together, does the model apparently learn a representation that no longer depends on any single discarded feature. UNSW→ transfer is workable for XGBoost (0.8116 F1, 0.7979 balanced accuracy) and marginal for the other two models; CIC→ collapses to chance for every model. One candidate explanation, consistent with the two datasets’ attack taxonomies (Sec. I-A), is a difference in attack character. CSE-CIC-IDS2018’s attacks are predominantly volumetric, comprising DDoS floods, HTTP floods, and brute-force attempts, all producing flows with anomalously high packet counts, byte counts, or throughput. A model trained on CIC may learn a decision boundary close to “attack = high volume.” That transfers poorly to UNSW-NB15, whose attacks (Exploits, Fuzzers, Reconnaissance, Shellcode, Backdoors) are comparatively quiet and behavioral: a single malicious probe, or an exploit riding a connection that otherwise resembles normal traffic. A volumetric decision rule finds nothing to flag in such traffic, and the observed recall of 0.032–0.039 in that direction is what such a rule would produce. The reverse direction transfers better under this account because UNSW’s more diverse, lower-volume attack types force a model to learn less volume-dependent patterns, some of which generalize to CIC’s DoS-like attacks. Computing per-subtype recall in both directions is a direct, low-cost extension that would resolve this. XGBoost’s F1 swings across roughly 38 points over the valid perturbation range while RoBERTa-LoRA’s moves by about 10. The shape of XGBoost’s curve is consistent with hard, axis-aligned tree splits. Once an interpolated flow crosses a learned threshold on a small number of high-importance features, the prediction flips discretely, producing the sharp fall by ε=0.20 =0.20 and the partial recovery at ε=0.40 =0.40 as different trees’ thresholds are crossed in different directions. That XGBoost’s precision holds near 0.99 throughout while recall collapses supports this reading: the perturbation moves attack flows across the boundary into the benign region rather than blurring the boundary itself. A complementary explanation for RoBERTa-LoRA’s comparative stability is that flow serialization (Sec. I-D) gives it access to structural patterns in the FEATURE=value text, including feature ordering, token structure, and the relative magnitude of adjacent fields, which a purely numeric interpolation perturbs less directly. VI Limitations Every RoBERTa-LoRA result reported in this paper reflects a single training run (Sec. I-D), unlike the classical arm, which is evaluated across four seeds (42–45). RoBERTa figures are reported as point estimates rather than as a mean with a standard deviation, and any comparison drawn against XGBoost or Random Forest in Sec. IV-D should be read with this asymmetry in mind. A different RoBERTa seed could shift the reported numbers, particularly in the cross-dataset condition, where the classical models themselves show meaningfully different variance across seeds (zero for XGBoost, 0.0830 for Random Forest). Multi-seed LLM evaluation with proper significance testing is the most direct way to strengthen the claims in this paper and is left to future work. RoBERTa checkpoints were selected by F1 on a 4,000-flow subset of the same held-out split subsequently used for reporting (load_best_model_at_end, Sec. I-D). Roughly 13% of each reported same-dataset evaluation set therefore participated in model selection, and the same applies to the benign half of the adversarial evaluation set. The classical arm used no validation-based model selection, so same-dataset and adversarial figures for the LLM arm may consequently be marginally optimistic relative to the classical arm. Cross-dataset figures are unaffected, as the target network is never seen during training or selection. The evasion attack in Sec. I-E perturbs flow features directly, subject to domain constraints. This guarantees that a perturbed flow’s features are plausible, but it does not guarantee problem-space realizability. An actual attacker would need to produce raw network traffic whose extracted NetFlow features match the perturbed values while still achieving the original objective, such as a successful DDoS or exploit. Pierazzi et al. [11] formalize this distinction, and their feature-space/problem-space framing is adopted throughout. Closing the gap typically requires an explicit problem-space attack construction, as in Venturi et al.’s structural, graph-based evasion attack against NIDS models [12], which is not implemented here. The results in Sec. IV-C should therefore be read as an upper bound on adversarial robustness, since some perturbations tested here may not be achievable by an attacker operating at the packet level. Broader surveys of adversarial machine learning in NIDS settings similarly emphasize that feature-space attacks must be evaluated against domain-specific feasibility constraints to be meaningful [13]. The attack drives every attack flow toward one point, the global benign centroid. This makes the attack cheap to specify and easy to reproduce, but perturbed flows become progressively less diverse as ε grows, degenerating entirely at ε=1 =1 (Sec. I-E). A stronger attacker would interpolate toward a nearby benign flow, or toward a cluster centroid chosen per attack flow, preserving diversity across the whole range and plausibly producing a harder evasion set. The reported robustness gap is specific to this centroid-directed attack and should not be assumed to generalize to per-flow or cluster-targeted variants. All findings in this paper are derived from exactly two networks. This is sufficient to demonstrate that cross-dataset transfer is directional and asymmetric, but not to establish how that asymmetry generalizes across networks more broadly. In addition, the pipeline evaluates only the binary label throughout (Sec. I-A), so transfer performance cannot be broken down by attack subtype. Recording attack subtype alongside the binary label, for diagnostic purposes only rather than as a training target, and computing per-subtype recall in both transfer directions is a concrete, low-cost next step that would confirm or overturn the volumetric-vs-behavioral account. The LLM arm uses a single architecture, RoBERTa-base with LoRA adapters (Sec. I-D). Other encoder architectures, larger models, and alternative fine-tuning strategies such as full fine-tuning, QLoRA, or domain-pretrained variants like SecureBERT are not evaluated. Prior work is mixed on whether this matters. Bui/Boffa et al. found that scaling to a much larger model (Mistral-7B) provided no benefit over BERT-base (−0.0%-0.0\% relative to the BERT baseline), and that domain-specific pretraining helped only marginally (SecureBERT +0.7%+0.7\%, UniXcoder +1.1%+1.1\%), which suggests the qualitative findings reported here may generalize across encoder-style LLMs. This has not been verified for this setting, and a decoder-only or larger encoder model could behave differently, particularly on the adversarial evasion axis, where the mechanism proposed in Sec. V is architecture-dependent by hypothesis. The distributed nature of the leakage signal uncovered in the ablation study (Sec. I-C) means some residual environment-correlated signal cannot be ruled out in Set C even after the staged removal. The near-zero movement in same-dataset F1 across all three ablation sets is consistent with this possibility and was not independently verified through a feature-attribution method such as SHAP. VII Conclusion XGBoost and RoBERTa-LoRA were evaluated across three axes, same-dataset performance, cross-dataset transfer, and adversarial evasion, and no universal winner emerged. The two models are tied same-dataset, XGBoost leads under distribution shift, and RoBERTa-LoRA leads under adversarial evasion at comparable false positive rates. Model choice for NIDS deployment should therefore follow the anticipated threat model rather than a single benchmark score. A single headline metric also proved insufficient even within an axis: the same false-positive diagnostic that confirms RoBERTa-LoRA’s adversarial robustness also reveals its cross-dataset F1 to be concealing a near-chance classifier. Feature-leakage removal does not improve cross-dataset transfer monotonically, indicating that the leakage signal is distributed across the feature representation. 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Rev., vol. 62, p. 100995, 2026. [Online]. Available: https://doi.org/10.1016/j.cosrev.2026.100995 LLM Usage Statement The authors used a large language model (Anthropic Claude) during the preparation of this work. Its use spanned three areas: (i) assistance with drafting and editing the manuscript text; (i) assistance with implementing, debugging, and refactoring the experimental pipeline; and (i) discussion and review of the experimental design and of the interpretation of results, including the identification of methodological issues in an earlier version of the evaluation protocol, specifically the attacks-only adversarial evaluation set and the degeneracy of the maximal-perturbation endpoint, which the authors then verified and corrected. All experiments were designed, executed, and validated by the authors. All reported numbers were produced by the authors’ own pipeline and independently checked against the recorded outputs. All cited works were verified by the authors against their published records. The authors take full responsibility for the content of this paper.

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