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Frontiers in Communications and Networks ·

Volume 7 - 2026 | https://doi.org/10.3389/frcmn.2026.1863367

Deployment-oriented evaluation of deep learning network intrusion detection systems

  • Kai Liang Lew1
  • Kok Swee Sim1*corresponding author
  • Hao Xian Cheong2
  1. 1Faculty of Engineering and Technology, Multimedia University, Melaka, Malaysia
  2. 2Faculty of Information Science and Technology, Multimedia University, Melaka, Malaysia
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Abstract

Deep learning models are now used as a security layer in network intrusion detection systems. These models are often used in Internet of Things (IoT), industrial Internet of Things (IIoT), software-defined networking (SDN), and future internet communication environments. Most of the models reviewed in literature are still trained and tested on the same dataset under closed-set evaluation conditions; these models are also required to tolerate traffic distribution changes, unseen attacks, and uncertain predictions. Review articles from 2024 to 2026 focus on three main concerns, namely, cross-dataset generalization under domain shift, open-set intrusion recognition, and reliability through calibration or uncertainty-aware evaluation. Many of the reviewed models have been developed using isolated datasets and assumptions that weaken direct comparisons among them. This makes it difficult to judge deployment readiness across other environments. Most studies in literature address only one of these concerns instead of all three; across 29 empirical studies published between 2024 and 2026, none have evaluated all three concerns together. Several of these studies report high benchmark accuracies, but the reviewed corpus lacks joint evidence that the models can handle new attacks and new datasets while remaining reliable in IoT, IIoT, SDN, and future internet environments. Future works therefore require better cross-dataset testing, more evaluations of unseen attacks, and reliability checks in real-world secure communication environments.

Keywords

1 Introduction

Deep learning network intrusion detection systems (NIDSs) are now used in modern networks, including Internet of Things (IoT), industrial Internet of Things (IIoT), software-defined networking (SDN), and future internet environments. Most of the studies reviewing these systems often report high benchmark results, but same-dataset improvement does not establish deployment readiness. Such models must also work when the networks experience traffic changes, unseen attacks, and uncertain confidence. Extant reviews show that there are four linked deployment gaps, including cross-dataset degradation (Cantone et al., 2024; Xin and Xu, 2025; Elangovan et al., 2026; Wu and Wang, 2026; Xu et al., 2025; Li et al., 2024; Zhang et al., 2025; Yu et al., 2025), closed-set failure under unseen attacks (Souza et al., 2025; Fang and Xie, 2025; Wu et al., 2024; Du et al., 2025; Nguyen and Le, 2025; Li et al., 2025), unreliable confidence or rejection (Talpini et al., 2024; Yang et al., 2024; Vij et al., 2024; Pal et al., 2025; Medjadba et al., 2025), and deployment adaptation in new environments (Bilal et al., 2026; Mazroa, 2026; Cerasuolo et al., 2025; Di Monda et al., 2024; Sri Abhijit et al., 2025; Zhu et al., 2024; Francis et al., 2026; Nguyen and Beuran, 2025; Al Rawajbeh et al., 2025; Ohtani et al., 2024).

Cross-dataset, open-set, and trustworthiness studies use different assumptions and goals. Some studies have combined two of these concerns (Talpini et al., 2024; Xin and Xu, 2025; Wu et al., 2024; Wu and Wang, 2026; Pal et al., 2025). Dataset construction, evaluation design, and training data choices also affect deployment performance (Pinto et al., 2025; Ha Thanh, 2026; Iwanowski et al., 2025). Some studies (Chinnasamy et al., 2025; Mutembei et al., 2025; Rehman et al., 2025) have provided review background on NIDS methods, datasets, metrics, challenges, and future directions. Our mini review explores whether recent (2024–2026) deep learning NIDS studies evaluate cross-dataset generalization, unseen-attack handling, and reliability using a single protocol; although these three concerns are the minimum requirements for predictive evaluations, they do not define full deployment readiness. Operational readiness also involves latency, throughput, resource consumption, and temporal drift considerations; it includes model updating, adversarial robustness, privacy, alert workload, and analyst integration. Within the reviewed corpus, the assessment protocols for cross-dataset evaluations, open-set detection, and reliability are not standardized. Figure 1 summarizes the workflow of the present review.

Deployment-oriented evaluation workflow and literature coverage gaps based on recent deep learning network intrusion detection systems (NIDSs). The upper layer involves source-dataset training and target-dataset testing. The middle layer entails unknown-attack withholding and confidence evaluation. The final layer shows the deployment-credibility decision. The dashed arrows indicate missing or weak links between evaluation checks when the studies test only one or two concerns instead of the full sequence. The bottom panel maps to the information in Table 1.
Figure 1. Deployment-oriented evaluation workflow and literature coverage gaps based on recent deep learning network intrusion detection systems (NIDSs). The upper layer involves source-dataset training and target-dataset testing. The middle layer entails unknown-attack withholding and confidence evaluation. The final layer shows the deployment-credibility decision. The dashed arrows indicate missing or weak links between evaluation checks when the studies test only one or two concerns instead of the full sequence. The bottom panel maps to the information in Table 1.

2 Literature search and selection

For our study, we selected published works from 2024 to 2026. The literature records were identified through a targeted scholarly search and verified against the final records available from journals, conferences, publishers, and digital object identifiers (DOIs). The search sources were Google Scholar, Crossref, IEEE Xplore, ACM Digital Library, ScienceDirect, and SpringerLink. The same Boolean query was used across all six sources with only source-specific syntax adjustments. The query was (“network intrusion detection” OR “NIDS” OR “network anomaly detection”) AND (“deep learning” OR “neural network”) AND (“cross-dataset” OR “domain shift” OR “domain adaptation” OR “open-set” OR “unknown attack” OR “0-day” OR calibration OR uncertainty OR abstention). The inclusion criteria were articles published from 2024 to 2026, articles within NIDS or network anomaly detection, and articles based on the use of deep learning or a deep-learning-centered hybrid model. Five studies without a deep-learning detector were retained as declared benchmarks or deployment-support exceptions (Cantone et al., 2024; Souza et al., 2025; Wu and Wang, 2026; Al Rawajbeh et al., 2025; Ohtani et al., 2024). Each article was also required to be related to at least one of the following deployment concerns: cross-dataset generalization; open-set or unseen-attack recognition; reliability through calibration or uncertainty, abstention, or deployment adaptation. The exclusion criteria were articles without any deployment relevance, cybersecurity papers outside NIDS, pre-2024 works, inaccessible full texts, insufficiently verifiable papers, and preprint articles. The publication window was specified as 1 January 2024 through 15 April 2026. The same concept groups were tailored to the search syntax of each source.

The retrieved set contained 198 records comprising 110 from Google Scholar, 37 from Crossref, 18 from IEEE Xplore, 6 from the ACM Digital Library, 18 from ScienceDirect, and 9 from SpringerLink. Duplicate records were removed using exact DOI matching, normalized title matching, and manual review. The titles were then converted to lowercase after removing any punctuation and extra spaces. When multiple versions existed for an article, the final peer-reviewed version was retained. This removed 27 duplicate records and left 171 records for title and abstract screening. The authors KLL and KSS screened their assigned records and discussed uncertain cases. This screening step resulted in excluding 71 records, advancing 98 works to full-text assessment, and retaining 2 articles for further checking, yielding a 100-record queue. Full-text assessment of this queue was not completed. The synthesis instead involved a separate curated evidence base of 29 full-text-verified empirical works without claiming that these were the only eligible ones among the 198 records. Two review papers and four context papers were used to provide the background and were not counted in the 29-paper empirical evidence base. Each empirical paper counted toward one primary role, with the secondary concerns being recorded separately. None of the studies included in the curated evidence base jointly evaluated cross-dataset generalization, unknown-attack rejection, and reliability under one unified deployment protocol.

The quality of each study was assessed in six areas, including data separation, leakage control, and target-domain access. The transparency of harmonization was also checked. The model, hyperparameter, and threshold selections were required to be independent of the test set. Lastly, statistical reporting with availability of data, code, and details were included. Our mini review does not involve training a model or selecting a new decision threshold. In the assessment of study quality, threshold selection was considered to be independent only when the training or validation data were used before held-out test evaluations; test-informed or unreported threshold selection were considered to lower confidence. We did not perform new statistical tests or a meta-analysis as part of this mini review. The statistical tests reported in the included studies were interpreted as within-study evidence only. A small number of folds or test runs and uncorrected pairwise comparisons were considered as limited claims of statistical superiority. The overall confidence was rated higher when the evaluation protocol was clear. There was no major leakage or test-informed selection. Repeat, statistical, or reproducibility support was present. The confidence was moderate if the results were still interpretable despite reporting or selection concerns; it was considered limited if a leakage, a test-informed selection, an unsupported claim, or a critical contradiction weakened the result. The inapplicable areas did not hurt the ratings, and the reported performance did not influence the study quality.

3 Deep learning methods in recent NIDSs

Convolutional neural networks (CNNs) capture local traffic patterns and long short-term memory (LSTM) networks capture sequence-level dependencies, while CNN-LSTM models combine both perspectives. Transformers capture long-range dependencies (Xin and Xu, 2025; Zhang et al., 2025), whereas graph-based models are suitable when traffic relationships need to be modeled (Wu et al., 2024). Cerasuolo et al. (2025) studied class-incremental network-agnostic NIDSs for adaptation to new benign traffic. Open-set recognition is used to classify known classes and identify unknown ones. Unknown-attack rejection is used to flag new attack families in NIDSs. Novelty detection is used to score the difference of a sample from its training data. Anomaly detection is used to distinguish normal from abnormal traffic. Out-of-distribution detection is used to find data outside the training distribution, including shifted benign traffic, shifted known attacks, or new attacks. Reliability is used herein as a general term for reliable model behaviors under these conditions. Calibration, uncertainty quantification, out-of-distribution detection, and abstention are used to assess different properties and are not interchangeable. Calibration is used to check whether the confidence matches the accuracy. Uncertainty quantification is used to estimate predictive uncertainty. Abstention means that a model declines a prediction when it lacks confidence.

Domain adaptation modules are used when the target datasets differ from the training datasets. Domain adaptation is not equivalent to source-only generalization and uses target-domain data during development. Unsupervised domain adaptation uses unlabeled target data, whereas supervised and few-shot adaptation use labeled target data. Target-specific features or label harmonizations are reported separately because they use knowledge of the target dataset. Adversarial alignment uses a domain classifier to ensure that the source and target features are similar (Li et al., 2024). Some studies report reduced gaps between the source and target datasets through Wasserstein alignment or non-linear explicit feature augmentation (Zhang et al., 2025; Yu et al., 2025), while other studies have examined invariant features across domains (Francis et al., 2026), few-shot multidomain feature fusion (Xu et al., 2025), and class-incremental adaptation (Cerasuolo et al., 2025). These methods are important when labeled target data are limited. Some recent works have considered deployment adaptation as part of the problem, in which the model must learn new benign traffic or new attack classes after training (Cerasuolo et al., 2025; Di Monda et al., 2024).

The reviewed corpus includes reliability modules and evaluations. Bayesian deep learning uses weight distributions instead of fixed values so that the predictions can include uncertainty (Talpini et al., 2024; Yang et al., 2024). Monte-Carlo dropout methods estimate uncertainty by running dropout at inference time (Medjadba et al., 2025). Calibration methods are used to assess or adjust predictive confidence, while abstention methods are used to decide when the model should refuse uncertain predictions (Vij et al., 2024; Pal et al., 2025). The prediction probability of a calibrated model should match its actual accuracy. These methods matter for cross-dataset generalization, unknown-attack handling, and reliable confidence.

4 Cross-dataset generalization

Source-only cross-dataset generalization is the first gap considered in our review. Here, a model is trained, selected, and calibrated using the source-domain data and then tested on a target dataset; no target examples are used for model fitting or adaptation. The reviewed reports show that the performance can decrease when a model is evaluated on another dataset. Elangovan et al. (2026) reported that the macro-F1 value reduced from the range of 0.84–0.96 under in-domain testing to 0.69–0.78 when the model was tested on the harmonized future internet IoT dataset; the study also produced a high benign false-positive rate of 0.30. In real traffic, benign flows are more common than attack flows, so even a small benign false-positive rate can cause more false alerts than true ones.

Not all studies on cross-dataset evaluations use a source-only condition. Xin and Xu (2025) reported that for a CNN-LSTM model with 99% accuracy, the cross-dataset test accuracy decreased and did not match the baseline in-domain accuracy; they reported that their cross-dataset Transformer-IDS improved the area under the curve (AUC) by approximately 10%–20% and F1-score by more than 10 points, in addition to improved probability-calibration and expected calibration error (ECE) results. Their calibration data source was inconsistent, so the result is not clear source-only evidence. Cantone et al. (2024) reported performance changes across different datasets; their within-dataset experiments showed high performances, including 9/16 experiments with Matthews correlation coefficient (MCC) values above 99.6%, but the average MCC reduced from 94.63% for the within-dataset case to 29.35% under cross-dataset testing. Several factors can reduce the performance, including dataset heterogeneities, redundancies, labeling issues, dataset-specific artifacts, different traffic statistics, feature definitions, class imbalances, and attack types. In our review, these numbers should be read as within-study evidence rather than direct rankings because the studies differ in terms of feature harmonization, source–target pairing, label mapping, test-set composition, possible dataset-specific artifacts or label-leakage risks, openness regimes, calibration or rejection thresholds, and access to target-domain information; they do not establish cross-study statistical superiority, deployment readiness, or generalizability beyond the evaluated datasets.

Reports have indicated reduced performance gaps when using alignment methods (Li et al., 2024), feature-space adaptation (Zhang et al., 2025; Yu et al., 2025), and few-shot learning (Xu et al., 2025); however, the results still show residual cross-dataset sensitivity. Three issues may contribute to these findings. First, the tools used to measure network features such as timeouts and packet counts use different rules to do this; this means that the feature data from different networks look very different and are hard to compare. Second, the models are prone to shortcut learning because the networks are overfitted to benign traffic footprints specific to the dataset, including IP subnets, operating system artifacts, and active ports, rather than learning generalizable security signatures. Third, the methods meant to align different data sources can trigger negative transfer under dissimilar source–target settings; this reduces the model accuracy when classifying known things, and the risk may be greater when the original and new data types are very different from each other. The TriHID method reported by Wu and Wang (2026) is prone to domain shift difficulties across its heterogeneous settings. Xu et al. (2025) reported few-shot adaptation with limited target data, which matters because new deployments may have limited labeled traffic for retraining. Deployment-adaptation-based approaches (Cerasuolo et al., 2025; Di Monda et al., 2024) have been examined for scenarios with scarce labels, benign traffic changes, or new attack classes after initial training. Thus, models that require thousands of labeled target flows may not be practical for new IoT or SDN environments.

5 Open-set intrusion recognition

The second gap considered herein is open-set intrusion recognition. A closed-set classifier is forced to assign every flow to one of the labels seen during training, even when the deployment traffic contains a new attack family. Souza et al. (2025) used a multiclass open-set classifier with a suspicious class instead of forcing every flow into a known attack label. Nguyen and Le (2025) reported separation of known and new attack classes in a discriminative projection space within their evaluated datasets. Fang and Xie (2025) and Li et al. (2025) have reported open-set or anomaly-oriented detection results when the training labels are limited. Wu et al. (2024) combined unknown-attack handling with cross-dataset evaluation instead of using open-set testing inside a single dataset. Du et al. (2025) argue that open-set recognition should not stop at rejection because the suspicious samples may still need inspection after detection. Most of the works on open-set intrusion recognition in the reviewed corpus assess novelty using dataset-specific protocols and not cross-dataset shift (Souza et al., 2025; Fang and Xie, 2025; Nguyen and Le, 2025; Li et al., 2025); only a few studies (Wu et al., 2024; Wu and Wang, 2026) have evaluated novelty alongside distribution shift. This offers limited evidence on whether an open-set IDS remains reliable when both the label and traffic distribution change at the same time.

6 Reliability and calibration

Reliability is the third gap considered in our review. High accuracy or F1-score values are not sufficient indicators of deployment reliability as they do not show calibrated per-flow confidence, stable decisions under distribution shifts, or safe abstention from uncertain predictions. Talpini et al. (2024) reported uncertainty-aware open-set and out-of-distribution (OoD) detection results for unknown-sample handling. Yang et al. (2024) studied Bayesian autoencoder uncertainty for anomaly detection; Vij et al. (2024) used reject-option logic to refuse uncertain predictions; Pal et al. (2025) combined calibration, uncertainty estimation, and OoD-style evaluation; Medjadba et al. (2025) used Monte-Carlo dropout and Bayesian model averaging to quantify uncertainty in SDN intrusion detection. Xin and Xu (2025) connected reliability with cross-dataset evaluation and reported improvements in ranking and calibration within their evaluated settings. Some deployment-oriented studies also examined operating conditions, including heterogeneous federated evaluation (Bilal et al., 2026), trustworthy IIoT deployment and explainability (Mazroa, 2026; Al Rawajbeh et al., 2025), poisoning-robust collaborative learning (Zhu et al., 2024), and low-label federated IoT settings (Nguyen and Beuran, 2025; Ohtani et al., 2024). Within the reviewed corpus, reliability remains weakly integrated with cross-dataset and open-set testing. One study on reliability that reported calibration or abstention only on in-distribution traffic did not show whether the method remained reliable under cross-dataset or unknown-attack stress. This is important because calibration can appear acceptable on familiar traffic but the model could stay overconfident on new or unseen data. Temperature scaling is normally fitted using held-out validation data; however, calibration can worsen when the data changes or new attacks appear, which makes the model’s predicted confidence less reliable.

7 Comparative analysis

The main categories reflect the primary evaluation purposes of each article. Articles on cross-dataset evaluations primarily focus on generalization across datasets or domains, while those on open-set evaluations mainly test unseen-attack, unknown-class, novelty, or open-world recognition. The papers on reliability mainly report testing calibration, uncertainty estimation, abstention, rejection, or confidence trustworthiness, while those on deployment adaptation mainly study practical operating conditions, such as federated learning, edge deployment, continuous update, robustness, low-label deployment, or heterogeneous environments. If a study also investigated another concern, this was recorded as secondary coverage and was not counted as another primary work. Table 1 shows the primary-category accounting of each work, so each article is counted only once even if it focused on more than one concern. Table 2 reports the deployment evidence matrix for the 29 empirical works.

TABLE 1. Taxonomy, core mechanisms, and deployment limitations of recent literature on deep learning NIDSs.

Primary frontCore mechanismStudyPrimary deployment limitation
Cross-dataset evaluationSource-only testing; target-informed harmonization; unsupervised adaptation; supervised or few-shot adaptationCantone et al. (2024); Xin and Xu (2025); Elangovan et al. (2026); Wu and Wang (2026); Xu et al. (2025); Li et al. (2024); Zhang et al. (2025); Yu et al. (2025)Target-domain access differs across studies, so the adaptation results are not directly comparable with source-only generalization results; most studies also lack unknown-attack and reliability evaluations under the same protocol
Open-set recognitionNovelty scoring; open-world anomaly detection; class-wise boundary estimationSouza et al. (2025); Fang and Xie (2025); Wu et al. (2024); Du et al. (2025); Nguyen and Le (2025); Li et al. (2025)Most studies use single-dataset holdout evaluations; only a few evaluate open-set rejection under domain shift
Reliability and calibrationBayesian networks; Monte-Carlo dropout; post hoc calibration; selective predictionTalpini et al. (2024); Yang et al. (2024); Vij et al. (2024); Pal et al. (2025); Medjadba et al. (2025)Evaluates calibration, uncertainty, out-of-distribution (OoD) scoring, or selective risk under different test conditions; Talpini et al. (2024) and Pal et al. (2025) included open-set or OoD stress, but these properties were not jointly evaluated under both cross-dataset shift and withheld unknown attacks
Deployment adaptationFederated learning; class-incremental updates; pruned edge backbones; robust poisoning defenseBilal et al. (2026); Mazroa (2026); Cerasuolo et al. (2025); Di Monda et al. (2024); Sri Abhijit et al. (2025); Zhu et al. (2024); Francis et al. (2026); Nguyen and Beuran (2025); Al Rawajbeh et al. (2025); Ohtani et al. (2024)Focuses on resource constraints or decentralized learning; many studies assume closed-set labels or clean target datasets

TABLE 2. Deployment evidence matrix for the 29 empirical works from 2024 to 2026. The reported values and statistical findings are within-study results and are not directly comparable across studies because the datasets, splits, openness settings, and metrics differ; these findings do not establish cross-study statistical superiority. The study-quality confidence reflects protocol clarity, leakage control, target-data access, selection procedures, statistical reporting, and reproducibility.

StudyReported result/valueFront testedStudy quality and deployment limitation
Cantone et al. (2024)Reported 9/16 within-dataset experiments with Matthews correlation coefficient (MCC) above 99.6%; the average MCC decreased from 94.63% for the within-dataset case to 29.35% under cross-dataset testing across the CIC/LycoS datasetsCross-datasetHigher confidence. The source-only cross-dataset protocol and data partitions were clear, although the single-attack analysis was reported to have the highest result from three runs. Dataset dependence was shown but unknown-attack rejection or reliability was not tested under the same protocol
Xin and Xu (2025)Reported Transformer-IDS cross-dataset gains, where the area under the curve (AUC) improved by approximately 10%–20% and F1-score improved by 10+ points over the baselines, along with improved probability calibration or expected calibration error (ECE) analysisCross-dataset + reliabilityModerate confidence. Three-seed variability and calibration metrics were reported, but the source of the calibration data for cross-dataset testing was described inconsistently. Pairwise evidence was provided but unknown-attack rejection was not tested in the same experiment
Elangovan et al. (2026)Macro-F1 drops from the range of 0.84–0.96 in-domain to 0.69–0.78 under future internet cross-dataset testing, with a benign false-positive rate (FPR) of about 0.30Cross-datasetModerate confidence. Source-only evaluation, training-only normalization, and fixed hyperparameters were clear. Results were reported across five independent runs with pairwise Wilcoxon signed-rank tests at p < 0.05, but the exact p-values, test sidedness, and correction for multiple comparisons were not stated. These tests are treated as within-study evidence and do not establish broad statistical superiority. Domain-shift risk was shown but this shift was not combined with unseen-attack rejection and calibration
Wu and Wang (2026)Evaluated multisource, semi-supervised, unsupervised, and open-set domain adaptation settings for IoT IDS.Cross-dataset + open-setModerate confidence. The target-access regimes were described, but repeated-run uncertainty and reproducibility resources were not reported clearly. There is useful benchmark evidence but reliability and abstention were not included as a third deployment requirement
Xu et al. (2025)Reported 99.03% accuracy (ACC) at K = 10 on CIC-IDS2017, 98.64% on CICIDS 2018, and more than 95.13% cross-domain ACCCross-dataset/few-shotHigher confidence. Target support access was explicit, results were averaged over ten trials, and source-only cross-domain testing was reported separately. The few-shot result was given, but the support/query setup was not a full source-only deployment test with unknown attacks and reliability checks
Li et al. (2024)Reported more than 95% average detection ACC across four IoT datasets under limited-sample tasksCross-dataset adaptationModerate confidence. Limited labeled target samples were used and experimental scenarios were disclosed, but reproducibility and conventional variability reporting remained limited. Domain adaptation was addressed but there was no joint evaluation of unknown attacks and reliability
Zhang et al. (2025)On UQ→CIC, authors reported ACC of 0.9234, F1-score of 0.9186, recall of 0.8639, AUC of 0.9468; average F1-score across 20 transfer tasks was 0.7791Cross-dataset adaptationLimited confidence. Unlabeled target data and pseudo-labels were used for adaptation. Scaling was described using all data, and important settings were selected using performance on reported target tasks. Shifted known-class detection improved but there were no tests for withheld unknown attacks or calibrated abstention
Yu et al. (2025)Reported more than 85% ACC under the difficult UNSW-NB15→CICIDS2017 cross-domain settingCross-dataset adaptationLimited confidence. The method used a labeled source and an unlabeled target, but the target samples used for adaptation were not clearly separated from target evaluation data, and the settings appear to be selected from target results. Targets domain mismatch but open-set rejection and reliability were not integrated
Souza et al. (2025)Reported area under the receiver operating characteristic curve (AUROC) of 0.859 and area under the precision–recall curve (AUPRC) of 0.993 on a reproduced CICIDS2017 open-set benchmark, with macro-F1 of 0.752 under closed-set testingOpen-setHigher confidence. Cross-validation, leave-one-class-out evaluation, a training-derived threshold, and reproducibility resources were reported. Useful open-set evidence was given, but a full deep learning joint deployment test with cross-dataset reliability was absent
Fang and Xie (2025)Reported ACC of more than 88.5% for misuse detection and more than 88.2% for anomaly detection on CICIDS2017 open-set testingOpen-setModerate confidence. Open-set construction was described, but the validation, OpenMax parameter selection, repeated runs, and code availability were insufficiently clear. Unknown-class handling was tested, but rejection stability under target-dataset shift was not shown
Wu et al. (2024)Reported OSDN open-set domain-adaptation results across source–target intrusion tasks, with ACC of 53.78–76.18 and IND-mode accuracy of 62.31–90.11 across openness settings up to 0.71Cross-dataset + open-setModerate confidence. Unlabeled target adaptation was explicit, but split selection, repeated runs, and variability reporting were limited. Pairwise evidence was shown but calibration, uncertainty, or abstention was not evaluated as the third requirement
Du et al. (2025)Improved open-recognition ACC over CADE by 1.08%–1.92% on USTC-TFC2016, 0.91%–3.21% on CIC-IDS2018, and 10.50% on TON-IoTOpen-set/inspectionModerate confidence. The known and unknown partitions were clear but key operating parameters were selected experimentally without an independent validation protocol. Unknown-sample inspection was included but cross-dataset reliability testing was not provided
Nguyen and Le (2025)Reported ACC of 97.12%–99.56% for multiclass classification, ACC of 94.53%–99.33% for novel-attack detection, and MCC of 0.825–0.975 for multiclass novelty detectionOpen-setModerate confidence. Leave-one-attack-out testing was clear but preprocessing fit and anomaly-threshold selection were not tied clearly to training or validation data. The result was novel but depended on selected novelty partitions and lacked cross-dataset calibration
Li et al. (2025)Reported CIC-IDS2017 F1-score of 95.2%/false omission rate (FOR) of 10.7% and kitsune F1-score of 83.2%/FOR of 15.8% under normal-only training; for real-vehicle data, the abstract reported an FOR of 13% while the main text reported an FPR of 0.130Open-set/anomalyLimited confidence. The anomaly threshold was not reported, attack-containing validation data served as the principal evaluation set, and vehicle evaluation was confounded by the experimental conditions. The findings are useful under normal-only training but closer to binary anomaly detection than full multiclass open-set deployment testing
Talpini et al. (2024)Evaluated uncertainty-aware out-of-distribution (OoD)/open-set detection on ToN-IoT and CICIDS 2017; detailed ToN-IoT 6U reports showed AUROC 20 * of 0.72 and AUROC of 0.92, while CICIDS results were averaged across scenariosReliability + open-setHigher confidence. Training, validation, testing, threshold selection, repeated runs, and uncertainty estimates were clearly separated and reported. Uncertainty was linked with unknown samples but not under full cross-dataset source–target shift
Yang et al. (2024)Reported AUC-rejection of 0.986±0.001 on UNSW-NB15 and 0.846±0.011 on CIC-IDS2017 using Bayesian autoencoder uncertaintyReliabilityModerate confidence. Seven-seed reporting was provided but model or distribution selection appeared to use the best observed result and code was not released. Uncertainty rejection was evaluated but unknown attack families and cross-dataset shift were not examined together
Vij et al. (2024)Reported base F1 values of 0.998, 0.994, 0.985, and 0.988; Wisdomnet reached near-zero or zero accepted-sample error under several settings at roughly 5%–7% rejection, while some uncertainty-threshold settings required higher rejectionReliability/abstentionModerate confidence. Validation-based thresholding and separate testing were reported, but repeated runs, statistical uncertainty, and code were absent. Rejection reduced the accepted-sample error, but the results depended on threshold and coverage choices
Pal et al. (2025)Reported ACC of 98.4%, false alarms of approximately 4.86% on IoT-23, selected calibration temperature T = 1.39, and retention of 96.42% at the top-F1 operating pointReliability + OoDModerate confidence. Calibration used a separate validation set but selective thresholds and OoD subsets appeared to be chosen from reported performance without repeated-run uncertainty. Reliability result was available but a full source–target protocol with withheld attack families was not provided
Medjadba et al. (2025)Reported 99.93% ACC and F1 on InSDN, and 99.89% ACC with 99.90% F1-score on CIC-DDoS2019 using CNN-LSTM with Monte-Carlo dropout and Bayesian model averagingReliability/uncertaintyLimited confidence. Normalization was described before data splitting, validation for model selection was unclear, and the claimed cross-dataset evidence consisted of separate within-dataset experiments. Uncertainty was quantified but cross-dataset generalization and unknown-attack rejection were not jointly tested
Bilal et al. (2026)Reported federated in-domain macro-F1 of up to 98%, cross-dataset drops of up to 30 percentage points, and 15%–25% communication reduction with FedNovaFederated deploymentModerate confidence. Feature and label harmonization were explicit, but communication-round counts were inconsistent and results lacked repeated-run uncertainty. Deployment realism was shown but federation was not combined with unknown-attack rejection and calibrated abstention
Mazroa (2026)Reported asymmetric cross-dataset transfer with F1 = 0.39 for DDoS→UNSW and F1 = 0.99 for UNSW→DDoS; replacing CNN-LSTM with a pruned CNN reduced median latency from 120 ms to 25 ms while ACC changed from 98% to 92%IIoT deployment/efficiencyModerate confidence. Leakage controls and multi-seed reporting were strong, but dataset counts and the role of target fine-tuning in the cross-dataset result were inconsistent. Deployment measurements were provided but the results did not cover the full cross-dataset, open-set, and reliability gaps
Cerasuolo et al. (2025)Reported cross-network class-incremental adaptation: in the multiclass setting, iCaRL+ provided approximately 5% DropOld and 4% DropAll; in the binary misuse-detection setting, the reported F1-score was approximately 99% and AUC was 100%Continuous adaptationLimited confidence. The training–testing partition and variability were not reported clearly, and target-network benign data were used for adaptation. Useful adaptation evidence was available, but a complete unknown-attack and calibrated-abstention protocol was not provided
Di Monda et al. (2024)Reported up to 95% F1-score on C all, up to +5% over the non-FSCIL baseline, and approximately 95% F1-score with a 10-s traffic-observation cutoffFew-shot class-incrementalModerate confidence. Training, validation, test, support, and query sets were separated, and 100 episodes were reported with confidence intervals. However, the 10-s observation cutoff was justified using the reported sensitivity analysis and not shown to have been fixed using training or validation data alone. The approach is useful for low-label attack adaptation but should not be treated as complete open-set reliability evidence
Sri Abhijit et al. (2025)Reported ACC/F1-score of 98.90%/95.79% on CSE-CIC-IDS2018, 98.70%/95.41% on UNSW-NB15, and 97.92%/94.56% on Edge-IIoTFederated transferLimited confidence. New-class arrival was inferred using label-dependent deployment metrics, weakening the claimed 0-day protocol, while split and variability reporting were unclear. Multi-dataset federated learning was shown but withheld unknown attacks and reliability were not shown under the same rule
Zhu et al. (2024)Reported robustness under three poisoning attacks, with approximately 93%–94% intrusion-detection ACC when up to 80% of industrial agents were maliciousRobust deploymentModerate confidence. Split, poisoning, and device conditions were reported, but the settings were selected from test-accuracy sensitivity and repeated-run uncertainty was not given. Poisoning robustness was addressed but cross-dataset open-set reliability was not explored
Francis et al. (2026)Reported merged-scenario accuracies of 99.73% on MQTT-bi, 99.77% on MQTT-uni, 99.79% on CICIDS 2017, and 98.31% on ToN-IoTFeature stability/deployment realismLimited confidence. The central source-to-target test was not performed, and the report contained contradictory descriptions of cross-domain evaluation. The findings are useful for scalability and invariant-feature analysis but not for a joint deployment-readiness test
Nguyen and Beuran (2025)Reported FedMSE AUC/ACC performance of 97.30±0.49 versus 93.98±2.90 in the high non-IID setting, with the same values under 50% gateway participationLow-label federated IoTHigher confidence. Training, validation, development, and test sets were separated, and five repetitions were reported with the released code and prepared data. The findings are relevant to practical IoT deployment but unknown-attack rejection and reliability remain separate
Al Rawajbeh et al. (2025)Reported 96.4% ACC, 2.1% FPR, and approximately 35 ms latency on raspberry pi 5 in IIoT deploymentEdge deploymentLimited confidence. SMOTE was explicitly applied before splitting, and the online stream used a labeled test-then-train procedure. Edge feasibility was supported, but latency and accuracy did not prove cross-dataset open-set reliability
Ohtani et al. (2024)Reported F1-score greater than 81% across DDoS, OSScan, ServiceScan, keylogging, and data exfiltration, with true-negative rate (TNR) greater than 0.91 in BoT-IoT-based IDAC scenariosFederated anomaly detectionModerate confidence. Scenarios and parameters were transparent, but the hyperparameters were chosen from the same attack-specific results used for reporting and detection variability was absent. Federated anomaly extraction was addressed but all three deployment fronts were not explored under one protocol

Although some studies examine two of the three deployment issues, these are only at the pairwise level. Xin and Xu (2025) combined cross-dataset evaluation with calibration-aware reliability evaluation. Wu et al. (2024) and Wu and Wang (2026) linked cross-dataset evaluation with open-set testing by examining unknown-attack handling under cross-domain variation. Talpini et al. (2024) and Pal et al. (2025) connected reliability with open-set or OoD-style stress but not under a full joint deployment protocol; the deployment-adaptation assessments add related but still partial evidence. Cerasuolo et al. (2025) examined cross-network benign traffic adaptation, while Di Monda et al. (2024) examined few-shot class-incremental attack adaptation. Although some of the studies on federated IDS (Bilal et al., 2026; Sri Abhijit et al., 2025; Nguyen and Beuran, 2025; Ohtani et al., 2024), trustworthy and robust deployment (Mazroa, 2026; Zhu et al., 2024), and IIoT edge-oriented deployment (Al Rawajbeh et al., 2025) further include examination of operational trust and robustness under constrained settings, they still leave at least one of the three deployment issues untested.

The limitation with the reviewed corpus is not just the weak models but also the lack of unified evaluations across the key deployment concerns. Works on cross-dataset evaluations (Cantone et al., 2024; Elangovan et al., 2026; Zhang et al., 2025; Yu et al., 2025) test how well the models transfer to different networks; however, these evaluations generally assume that all attacks are known and do not measure confidence. Works on open-set evaluations (Souza et al., 2025; Fang and Xie, 2025; Nguyen and Le, 2025; Li et al., 2025) test for rejection of unknown attacks; however, these tests usually involve only one dataset, so their rejection settings are not checked against changing environments. Works on reliability (Yang et al., 2024; Vij et al., 2024; Medjadba et al., 2025) report the ECE or uncertainty scores, but these metrics are measured only on data that the model is familiar with.

8 Limitations, open problems, and future evaluation directions

Reproducibility support is uneven across the reviewed corpus because the reported training–testing splits, label harmonization rules, and held-out attack designs are inconsistent. Further, the dataset coverage in the corpus is narrow; most of the reported results are based on CIC-IDS2017, UNSW-NB15, NSL-KDD, and limited IoT captures while newer internet traffic remains underused. The open problem here is not another isolated architectural gain but a joint deployment evaluation design. Future studies should combine the three specific checks (cross-dataset shift, withheld unknown attacks, and reliability assessment) in a single protocol. Without cross-dataset testing, source-specific overfitting and failure cannot be ruled out in new environments. Without open-set testing, generalizing the models may forcefully classify novel 0-day attacks into known labels, creating severe security blind spots. Without calibration and selective prediction, the models may yield overconfident and incorrect classifications on shifted benign traffic. Thus, a joint evaluation protocol would provide stronger evidence of model usefulness under distribution shift, unseen attacks, and uncertain predictions; while these three checks are essential for assessing the predictive scope of a review, they do not equate to full deployment readiness.

We propose a joint protocol with a four-step pipeline for future deployment-oriented evaluations. First, the NIDS model would undergo predeployment offline training and post hoc calibration to establish the baseline confidence curves. Second, the model would be integrated inline at the network gateways to predict labels and output calibrated confidence scores for the incoming flows. Third, the system would apply dual-path decision routing such that the high-confidence predictions are automated while the low-confidence predictions and open-set detections are routed to security analysts or deep-packet inspection tools. Fourth, the flagged anomalies would be labeled periodically and integrated back into the system via class-incremental updates and recalibration cycles. This pipeline is a review recommendation at present and was not validated in this study. Figure 2 summarizes this joint deployment-oriented protocol.

Joint deployment-oriented evaluation protocol for a deep learning NIDS. The same trained model is evaluated under source–target dataset shift, predeclared withheld unknown attacks, and calibration or abstention testing. A strong predictive evidence necessitates three checks in a single run, namely, known-class performance, unknown-attack rejection, and confidence or abstention. Full deployment readiness is not achieved by passing these checks alone; operational and lifecycle factors are also key to the evaluations.
Figure 2. Joint deployment-oriented evaluation protocol for a deep learning NIDS. The same trained model is evaluated under source–target dataset shift, predeclared withheld unknown attacks, and calibration or abstention testing. A strong predictive evidence necessitates three checks in a single run, namely, known-class performance, unknown-attack rejection, and confidence or abstention. Full deployment readiness is not achieved by passing these checks alone; operational and lifecycle factors are also key to the evaluations.

The protocol should specify three things. First, fixed source–target dataset pairs should be used, such as CIC-IDS2017 to CSE-CIC-IDS2018 or UNSW-NB15, CIC-IDS2017 or CSE-CIC-IDS2018 to CICIoT2023 or CIC-DIAD2024, and Bot-IoT or TON-IoT to Edge-IIoTset, CICIoT 2023, or TII-SSRC-23. This should be implemented under explicit feature and label harmonization rules, as shown in recent cross-dataset studies (Cantone et al., 2024; Xin and Xu, 2025; Elangovan et al., 2026; Wu and Wang, 2026) and dataset-framing works (Ha Thanh, 2026; Iwanowski et al., 2025). Second, at least one attack family should be withheld from training, such as DoS/DDoS, botnet, scanning or reconnaissance, brute force, infiltration, or IoT malware, depending on the dataset. The study should report the known classes, withheld attack families, numbers of known and unknown classes, and openness ratio in accordance with the motivations of open-set studies (Souza et al., 2025; Wu et al., 2024; Nguyen and Le, 2025) and open-set inspection works (Du et al., 2025). Third, calibration and abstention metrics, such as ECE, minimum classification error, Brier score, area under the accuracy–rejection curve or area under the risk-coverage curve, selective risk, and coverage-risk curve, should be reported for shifted and unknown-attack cases, not just in-distribution traffic (Talpini et al., 2024; Xin and Xu, 2025; Vij et al., 2024; Pal et al., 2025; Medjadba et al., 2025). All classification, novelty, rejection, and abstention thresholds should be selected using only training or validation data before held-out test evaluations. The source-only claims should not use target test data for threshold selection. Lastly, statistical comparisons should report the number of folds or runs and any corrections for multiple pairwise comparisons.

9 Conclusion

The performance of a deep learning NIDS should not be judged on only same-dataset benchmarks. The studies reviewed herein report improvements in cross-dataset generalization, open-set recognition, or reliability, but these deployment problems are mostly addressed in isolation. Hence, future deployment evaluations should integrate cross-dataset evaluation, unknown-attack testing, and reliability assessment; this would provide stronger evidence on whether deep learning NIDSs remain useful under multi-environment conditions.

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Footnotes

Edited by: Qasem Abu Al-Haija, Jordan University of Science and Technology, Jordan

Reviewed by: Hani Iwidat, Al Istiqlal University, Palestine

Ahod Alghuried, Prince Sattam Bin Abdulaziz University, Saudi Arabia

Malik AL-Essa, Al-Zaytoonah University of Jordan, Jordan

Azhagiri M, SRM University, India

Statements

Conflict of interest

The author(s) declared that this work was conducted in the absence of any commercial or financial relationships that could be construed as a potential conflict of interest.

Funding

The author(s) declared that financial support was not received for this work and/or its publication.

Author contributions

KL: Methodology, Formal analysis, Validation, Data curation, Conceptualization, Investigation, Software, Visualization, Writing – original draft, Writing – review and editing. KS: Resources, Funding acquisition, Project administration, Writing – review and editing, Supervision. HC: Writing – review and editing.

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Citation

Lew, K. L., et al. (2026). Deployment-oriented evaluation of deep learning network intrusion detection systems. Frontiers in Communications and Networks, Volume 7. https://doi.org/
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7 - 2026

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Copyright © 2026 Lew, Sim and Cheong.

License: https://creativecommons.org/licenses/by/4.0/

*Correspondence: Kok Swee Sim

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