Most explainability research follows a familiar pattern: propose a new method, demonstrate it on benchmark datasets, report a faithfulness score, and publish. The problem, as this position paper from arXiv (arXiv:2607.14123) argues with some force, is that this pattern has produced an enormous catalogue of techniques that practitioners largely ignore. Explanations get generated and discarded. They rarely change decisions. The field has been building floors without first laying a foundation.
This is a position paper, so it does not introduce a new algorithm or benchmark. What it offers instead is a diagnosis of why the XAI field has stalled despite genuine methodological creativity, backed by an analysis of recent papers from ICML, NeurIPS, and ICLR alongside a practitioner survey. The diagnosis is uncomfortable but hard to dismiss.
The Core Argument
The authors contend that explainability research has inverted the natural order of scientific progress. Methods have been developed before the field has agreed on what explanations are for, what properties they must satisfy, or how to evaluate whether they actually help anyone. This inversion means results cannot accumulate meaningfully. You cannot compare two methods if there is no agreed definition of success.
Four interdependent challenges are identified, each blocking progress on the others:
- Definitions: What does it mean to explain a model? The answer depends entirely on who is asking and why. A debugging engineer, a regulatory auditor, and a clinical decision-maker need fundamentally different things. Current methods rarely specify which of these they are targeting.
- Properties: Faithfulness (does the explanation actually reflect the model's behaviour?) is necessary but not sufficient. Completeness, robustness, and actionability are also required, yet these properties are rarely defined precisely enough to test rigorously.
- Evaluations: The paper identifies a troubling gap between automated metrics and real-world utility. Practitioners are not using the metrics academics produce. The survey found that only 35.3% of practitioners use quantitative measures of explanation quality, while nearly half reported simply not knowing how to check whether an explanation is good.
- Applications: Explanations are almost universally treated as standalone outputs rather than components of iterative, feedback-driven workflows. There are almost no established pipelines connecting explanation to human feedback to model or system update.
The authors are careful to distinguish their target. They are not criticising mechanistic interpretability research aimed at scientific understanding of deep learning systems. The critique is directed at methods that claim explanatory utility for downstream stakeholders but cannot demonstrate it.
Methodology and Evidence
The empirical grounding is worth examining. The paper combines a literature analysis of recent top-venue ML papers with a practitioner survey. This is a sensible combination: the literature analysis identifies what researchers claim, and the survey reveals what practitioners actually experience. The finding that practitioners largely bypass academic metrics because those metrics have no proven relevance to real workflows is the kind of evidence that should be difficult to ignore.
The evaluation critique is the most technically developed section. The authors propose distinguishing three levels of evaluation: formal property guarantees under stated assumptions, functionally-grounded automated metrics, and empirical evaluation with human stakeholders on concrete tasks. The problem is that current practice treats these as separate silos rather than a connected pipeline. Researchers optimise faithfulness scores without checking whether high faithfulness scores predict better debugging outcomes. The authors call this a "phantom" category of evaluation: mathematically precise but practically meaningless.
Their proposed remedy is task-grounded objective evaluation, where automated metrics are explicitly validated as proxies for performance on a specific downstream task. Rather than assuming sparsity or stability are universally desirable, these properties become hypotheses to be tested empirically for each application context. This is a sensible reframing, though it substantially raises the cost of doing XAI research properly.
What the Paper Gets Right
The human-centricity argument is well-made. Explainability is not a property of a model in isolation; it is a relation between a model, an explanation, and a person with a specific goal. This is not a new observation, the human-centered XAI community has been making it for years, but the authors are right that it remains systematically underspecified in ML-community XAI papers. A method that produces beautiful saliency maps which no radiologist can act on has not solved the problem.
The checklist provided at the paper's conclusion is practically useful. It prompts researchers to specify their target stakeholder, the intended use of the explanation, the properties being claimed, and the evaluation approach. Treating this as a submission requirement at major venues would improve the field's coherence considerably.
The open problems listed are also well-chosen. The question of how to systematically select free parameters in XAI algorithms (perturbation type in LIME, sparsity ratio in sparse autoencoders) is genuinely underexplored and has real consequences for explanation stability. The call for an "ImageNet for XAI" reflects a real need, though designing such a benchmark without first solving the definition problem would reproduce exactly the error the paper is criticising.
Limitations and Open Questions
Position papers carry inherent limitations. The practitioner survey results are cited but the survey methodology is not described in detail in the sections available here, which makes it hard to assess how representative the sample is or whether response bias might be shaping the conclusions.
There is also some tension in the argument. The authors acknowledge that practitioners may find utility in current tools and explicitly do not call for a halt to methods development. But if the field's evaluation apparatus is as broken as they argue, it is genuinely unclear how practitioners are identifying which tools are useful. The paper does not fully resolve this.
The task-grounded evaluation proposal is appealing but the resource burden is real. Empirical evaluation with domain experts on concrete tasks is expensive and slow. The paper gestures toward this as a complement to automated metrics rather than a replacement, but the practical path from current practice to this vision is not fully sketched.
Finally, the scope of the critique is primarily the ML community's approach to XAI. The HCI and CSCW communities have been doing human-centered evaluation of explanations for longer, and the relationship between those bodies of work and the agenda proposed here deserves more explicit treatment than it receives.
None of this undermines the central claim. The XAI field has produced an impressive volume of methods whose real-world impact remains difficult to measure and largely undemonstrated. Redirecting effort toward foundational clarity, rigorous evaluation frameworks, and end-to-end deployment pipelines is the right prescription. Whether the community will act on it is a different question. Read the full paper at arxiv.org/abs/2607.14123.