Over the past five years, a specific analytical routine has become the default way to claim that a fluorescence sensor can tell chemically similar compounds apart. The material is exposed to a panel of analytes, emission intensities are recorded at two or more wavelengths, the response vectors are projected through principal component analysis (PCA) or hierarchical cluster analysis (HCA), and separated groups in the resulting plot are presented as evidence of discrimination. This workflow has distinguished antibiotic classes [1], structurally related drug candidates and their metabolites [2], natural product families [3], and co-occurring contaminants or metal ions in complex matrices [4][5]. Lanthanide metal-organic frameworks (Ln-MOFs), with their sharp, spectrally separable 4f-4f emission bands and amenability to dual-lanthanide co-doping, have become a favored platform for this kind of multiplexed sensing [1][2][5], and publication in this niche has accelerated sharply since 2023.

Part of the platform’s appeal is mechanistic flexibility, which gives researchers design freedom but also freedom in how a response gets explained after the fact. Reported quenching behavior ranges from the inner filter effect alone [6], to the inner filter effect confirmed by density functional theory while photoinduced electron transfer and Förster resonance energy transfer are both ruled out by lifetime measurements [7], to the inner filter effect and photoinduced electron transfer acting together [8][9], to three mechanisms invoked at once [10]. A bimetallic probe for malachite green showed that a monometallic version of the same material relies on the inner filter effect while its bimetallic counterpart shifts toward resonance energy transfer, improving the detection limit roughly a hundredfold in the process [11]. Two recent reviews confirm this mechanistic diversity is now the norm rather than the exception across the fluorescent MOF literature [12][13]. The flexibility is a genuine strength, but it means mechanism attribution rests on an unevenly supported evidence base, spectral overlap alone in some studies, lifetime or computational confirmation in others, a parallel inconsistency worth flagging even though it sits outside this paper’s scope.

These are not academic distinctions. Fluoroquinolone and nitrofuran residues carry regulatory maximum residue limits and feed antimicrobial resistance selection at sub-therapeutic exposure, which is why resolving structurally related congeners, rather than only flagging one compound, has become a stated design goal in its own right [1][8][9]. The same logic drives food-adulteration arrays asked to separate a dye from its reduction product or from co-administered antibiotics in the same matrix [6][11], and clinical arrays tested against ten-ion metal panels [5] or mixed drug panels [2] in matrices meant to approximate real physiological samples rather than clean buffer. Because a maximum residue limit either is or is not exceeded, and a metabolite either is or is not distinguishable from its parent compound, a discrimination claim needs to rest on something more defensible than a plot that merely looks convincing.

What has not kept pace is the statistical rigor behind the claim itself. A separated cluster visualizes variance; it is not a validated measure of discriminatory power. It says nothing about whether the separation would survive a blind sample, hold across the working concentration range rather than at one convenient level, resist realistic instrument drift or matrix noise, or exceed a distance large enough to be meaningful rather than merely visible. These are answerable questions, and a handful of studies have already answered some of them, through blind sample accuracy statistics [1], concentration-independent testing across multiple orders of magnitude, or explicit noise robustness checks. But these practices remain scattered rather than shared, and no two papers report the same combination, which makes cross-study comparison of discriminatory power largely impossible.

This paper does not propose a new sensor. It proposes that the field agrees on what counts as evidence. We first characterize the current spread of validation practice across recent Ln-MOF sensor array literature, then identify five specific and recurring gaps, and finally propose a minimum reporting checklist that could be adopted without new experiments in most cases, since the required calculations can usually be performed on data already collected.

This was a narrative mini review. Searches were executed in January 2026 in PubMed, Embase, Scopus, Web of Science, and Google Scholar for records published between 2020 and 2026 using combinations of the terms lanthanide MOF, Ln-MOF, fluorescent sensor array, ratiometric sensor array, PCA discrimination, and HCA antibiotic, and supplemented with citation chaining from two recent field-wide reviews [14][15]. Records were included if they reported an Ln-MOF-based fluorescence sensor system evaluated against two or more analytes using PCA, HCA, or an equivalent multivariate discrimination method, and were excluded if they described a single-analyte sensor with no discrimination claim, a non-lanthanide or non-MOF material, a conference abstract without an accessible full text, or a study duplicated across databases. Title and abstract screening against these criteria was performed by the author, followed by full-text assessment of the retained records; ambiguous or borderline cases (for example, studies reporting differential quenching across analytes without an explicit multivariate discrimination step) were resolved by re-reading the methods and results sections against the inclusion criteria above. This approach was chosen to capture the most active recent portion of a fast-growing subfield rather than to provide an exhaustive, PRISMA-style census, and no formal risk-of-bias tool was applied. The 27 sources discussed in this paper, drawn from that search, illustrate a pattern we believe is representative of current practice, not a complete accounting of every Ln-MOF sensor array paper published in this window; a full record of search strings, per-database hit counts, and screening decisions is provided in Appendix alongside the study-level checklist extraction described in Section 4.

Looking across the Ln-MOF sensor array literature published in the last five years, validation effort is not absent, but it is unevenly distributed and rarely cumulative. Most papers stop at the same point: a PCA score plot or an HCA dendrogram in which the analyte groups do not visually overlap, described in the text as well separated or clearly discriminated. The strength of that separation is almost never expressed as a number.

A smaller group of studies goes further and tests the model against samples it was not trained on. Xie et al. built a ratiometric Eu/Tb-MOF array that classified 25 antibiotics from eight structural classes using the emission ratio at 545 and 616 nm, then challenged the model with 48 blind samples and reported 98 percent correct identification [1]. A related array built from four Ln-MOFs and applied to 26 natural product ingredients was similarly tested against blind samples and reported 100 percent accuracy [3]. These two studies are useful reference points precisely because blind testing is still the exception rather than an expected step. Most papers in the same window report only the training-set clustering that produced the model in the first place, which is a weaker claim than it is usually presented as, since a model will almost always separate the data it was built from.

A separate axis of rigor concerns how the classification accuracy itself is reported. Wang et al. paired a bimetallic EuxTb1-x-MOF array with PCA and HCA to identify prostate cancer drugs and their mixtures, and supported the assignment with density functional theory calculations of the underlying interaction, which strengthens the mechanistic case even where the statistical case is left mostly visual [2]. A more recent pH-regulated lanthanide array aimed at ten metal ions in biological fluids used PCA together with an Extra Trees classifier and reported a confusion matrix for the ten-way classification, along with separate testing on binary and ternary mixtures [5]. A confusion matrix is a meaningfully different kind of evidence than a score plot, since it quantifies exactly which analytes are confused with which, at what rate, rather than asserting that no confusion is visible.

Real-matrix and field-relevant testing follows its own inconsistent pattern. A dual-emissive single-component MOF array was shown to distinguish 12 antibiotics and was also described as having robust quantitative performance for individual compounds [16]. That phrasing blends two distinct claims, classification of identity and quantification of concentration, without separating the evidence for each. A Tb-MOF array built for nitrofuran antibiotics reported discrimination of both individual compounds and their binary and ternary mixtures, together with a portable paper-based readout validated in real food samples [17]. This is a strong showing on field applicability, but it does not report a numerical separation metric for the mixture discrimination claim. A 3D-printed smartphone platform aimed at two structurally similar fluoroquinolones combined a self-calibrating lanthanide sensor with PCA to achieve discrimination and reported point-of-care operation in environmental water [18]. Again, no quantitative index of how far apart the two clusters actually sit is reported. A related water-stable Tb-MOF was reported to discriminate three separate classes of antibiotics as well as D₂O from H₂O using a self-calibrating ratiometric response [19]. The discrimination is described as fast, accurate, and highly sensitive, but as with several examples above, those adjectives are not accompanied by a computed distance or accuracy figure that would let a reader judge the claim independently of the authors’ own description.

Two broad reviews published within the last several months, one surveying optical sensing arrays across material classes [14] and one focused on porous-framework arrays and their AI-assisted analysis [15], confirm that this is now a large and fast-moving subfield rather than a marginal one. Neither review, however, audits the internal consistency of how discrimination is validated across the primary studies it covers.

Two further cases sharpen the picture. Zhang et al. constructed six isostructural lanthanide MOFs and used PCA to distinguish Fe³⁺, two chromium oxyanion species, and ceftriaxone sodium in water, alongside separate ratiometric detection of uric acid in simulated urine. The authors describe the work as the first MOF sensor to use PCA for differentiating water contaminants [4]. The claim of novelty is plausible, and the recovery data for uric acid are solid, 95.08 to 102.07 percent, with an RSD below 2.63 percent. But the PCA-based discrimination of the four water contaminants is again reported through score-plot separation alone, with no accuracy statistic attached to the classification itself. A more recent hydrogel-based kanamycin sensor takes the opposite approach to sophistication: it layers four detection modes, single-emission screening, self-calibrated ratiometric sensing, full-spectrum machine learning analysis, and smartphone readout, into one hierarchical workflow [20]. This is a meaningfully more rigorous architecture than most array papers attempt, since each mode is positioned to cross-check the others rather than standing alone, and it points toward where the field is heading. But it is also, at the time of writing, closer to an isolated example of best practice than a reflection of what is typically expected of a new sensor array submission.

Taken together, these additional cases reinforce rather than complicate the pattern established above. Rigor is increasing at the frontier of the field, largely through machine learning and multimodal cross-checking. But the median paper still relies on visual cluster separation as its primary or sole evidence of discriminatory power. The inconsistency is not a matter of a few outlier studies falling short. It is that no shared minimum standard exists for what a validated discrimination claim should contain, which makes the frontier and the median difficult to compare on equal terms. The following section breaks this inconsistency down into five specific, recurring gaps.

Figure 1 maps these gaps onto the workflow itself, showing where each one

Figure 1. The standard sensor array workflow, and where its validation evidence usually stops.

typically opens up between an accepted step (solid boxes) and the validation evidence the checklist in Section 4 asks for (dashed boxes). The five subsections below discuss each gap in turn.

The gaps identified above are not evenly weighted. Some, such as reporting a quantitative separation metric, require no new data collection at all, only a different treatment of results already in hand. Others, such as blind sample testing or noise-injection robustness checks, require modest additional experimental or computational effort but nothing approaching the scale of a new synthesis or a new sensing platform. What follows is a proposed minimum set of nine criteria, framed as a checklist rather than a formal standard, that a study reporting a multi-analyte discrimination claim for a fluorescence sensor array could reasonably be expected to address, either by satisfying the criterion or by explicitly stating why it does not apply (Table 1).

The checklist is deliberately narrow in scope. It does not attempt to specify sensor design, material choice, or analyte selection, since those decisions are legitimately driven by the scientific question a given study is asking. It concerns only the evidentiary basis for a discrimination claim once that claim is made, on the reasoning that a reader should be able to judge how much confidence a cluster separation deserves without needing to reconstruct the underlying statistics from a figure.

To move beyond descriptive language such as rare or occasional, we applied the nine criteria retrospectively to the studies audited in Section 2. Of the 27 primary and review sources cited in this paper, 17 report an explicit multi-analyte discrimination claim and were included in this count; the remainder are cited either for mechanistic context (quenching pathway studies not making a discrimination claim) or as broad field reviews rather than primary discrimination studies. For each of the 17, a criterion was scored as satisfied only where this paper’s review explicitly describes that evidence being reported, and scored as explicitly absent only where the review explicitly states the evidence is missing. Where our review of a given study did not address a criterion one way or the other, the case is recorded as not addressed rather than assumed absent, since the absence of a statement is not equivalent to a confirmed gap. This distinction matters: the counts below likely understate true coverage of criteria 2 and 7 in particular, since replicate counts and dedicated mixture-calibration models are reported in methods sections that fell outside the scope of what this review discusses for each paper. A full accounting of those two items would require a dedicated re-read of each paper’s methods section, which we flag as a limitation of this table rather than a claim that the field performs better on those two items than it does on the rest. The per-study scoring underlying the aggregate counts in Table 1, together with the specific text passage used as evidence for every satisfied or absent call, is provided in full as Appendix, so that any individual cell in Table 1 can be traced back to the study and statement that produced it rather than taken on the authors’ summary alone.

None of these nine items is unprecedented. Each has already appeared, individually, in at least one of the studies audited in Section 2: blind testing with an accuracy figure in the antibiotic and natural product arrays [1][3], a confusion matrix in the ten-metal-ion array [5], multimodal cross-checking in the hydrogel kanamycin sensor [20], and real-matrix testing in the nitrofuran paper-based array [17]. What is missing is not any single technique, but the convention of applying more than one or two of them together and reporting the result plainly enough that a reader unfamiliar with the specific material can judge the strength of the discrimination claim without re-deriving it.

Item 7 deserves a brief note, since it is the criterion most likely to be contested. Not every study needs to quantify mixture components; a sensor intended purely for screening or triage may only need to answer a yes-or-no or which-of-several question, and demanding a full calibration model in that case would be disproportionate. The criterion is phrased conditionally for this reason: it applies only where a quantification claim is actually made. The problem identified in Section

Table 1.Proposed minimum reporting checklist for multi-analyte discrimination claims in fluorescence sensor arrays.

Note. The reporting checklist is mapped to the corresponding gap identified in Section 3, with a retrospective count against the 17 primary discrimination-claim studies audited in this paper.

3.5 is not that quantification is attempted and falls short, but that the word is used without the corresponding evidence being present at all.

Item 2 deserves a similar note. The floor of three independent replicates is not proposed as a formal power calculation, but as the minimum number of measurements from which any variance or outlier can be assessed at all; below three replicates, a response vector’s spread cannot be estimated, only assumed. This floor is consistent with long-standing convention in single-laboratory method validation, where replicate measurement in triplicate or more is treated as a baseline requirement for estimating precision [30]. Studies working near the limit of detection, or with material that is expensive or difficult to synthesize in bulk, may reasonably need more replicates rather than fewer to characterize response variability adequately. There is proposed here as a minimum below which a discrimination claim should be treated cautiously, not as a target that on its own guarantees sufficiency.

Two of the nine items, numbers 1 and 6, are proposed here as the practical starting point. Both can typically be satisfied through re-analysis of data a study has already collected, cost almost nothing in additional experimental time, and would on their own resolve the two gaps that recur most consistently across the literature audited in Section 2. A reviewer or editor who begins by asking for these two alone would already shift the baseline for what a discrimination claim is expected to demonstrate.

To show that the checklist in Section 4 is operational rather than aspirational, it is useful to apply it directly to two of the papers already introduced in Section 2, chosen because between them they satisfy more of the nine criteria than most single papers in this literature, which makes them a fair test of what the checklist rewards and what it still catches.

The ratiometric Eu/Tb-MOF antibiotic array of Xie et al. [1] is the strongest available example against criterion 3. After building a classification model from the F545/F616 response of 25 antibiotics across eight structural classes, the authors challenged that model with 48 blind samples and reported 98 percent correct identification. This is a direct, textbook satisfaction of the blind-testing requirement described in Section 3.1: the accuracy figure describes performance on data the model did not see during construction, not on the training set itself. The same study also reports testing in the presence of interfering substances and quantitative recovery for antibiotic mixtures in real water samples, which speaks partially to criterion 8. What the paper does not report is a numerical cluster-separation index for the PCA space itself, criterion 1, or a robustness check under deliberately injected signal noise, criterion 5, so a checklist-based read of this study would credit it clearly on blind validation while still flagging two open items.

The pH-regulated lanthanide array aimed at ten metal ions in biological fluids [5] offers a complementary strength. Its PCA and Extra Trees classification are backed by an explicit confusion matrix for the full ten-ion discrimination task, which satisfies criterion 9 far more precisely than a score plot alone: a confusion matrix shows exactly which ion pairs are occasionally misclassified and at what rate, rather than only asserting that the ten clusters look separated. The same study tested classification at three separate concentrations, 100, 25, and 10 micromolar, for each ion, which goes some way toward criterion 4, and extended testing to binary and ternary mixtures, which addresses part of the concern in Section 3.5 by treating mixture discrimination as its own tested condition rather than an extrapolation from single-analyte results. What remains unclear from the available reporting is whether the ion identification claim and any associated concentration values are backed by separate calibration evidence, or whether, as in several studies audited in Section 3.5, the two claims are presented together without being separately validated.

Read side by side, these two studies show that no single paper in this literature currently satisfies the full checklist, but that most of it is already achievable using techniques already in active use somewhere in the field. Neither the blind-sample accuracy statistic in the antibiotic array nor the confusion matrix in the metal ion array required a new sensing platform to produce; both are analytical choices made after the same kind of fluorescence titration data that nearly every study in this space already collects. That is the more general point the two examples are meant to illustrate: the checklist is not asking the field to do harder chemistry, it is asking the field to stop treating a subset of already-available statistical practice as optional.

Analytical and clinical research have been through this kind of correction before. Quantitative PCR faced a similar problem in the early 2000s, when a proliferating literature reported cycle threshold values and fold-change claims without a shared minimum standard for what counted as an adequately validated result. The response was not a new instrument or a new chemistry, but a published checklist, MIQE, specifying the minimum information an experiment needed to report before its quantification claims could be taken at face value [31]. A comparable movement took hold in diagnostic accuracy research through the STARD statement, which set out the essential items a study needed to report before a diagnostic test’s accuracy could be evaluated on equal terms across publications [32] and more broadly across biological and biomedical fields through the MIBBI initiative, which coordinated a family of minimum-information checklists spanning multiple experimental domains under the shared premise that a result is only as comparable as its reporting is complete [33]. A related precedent exists for a different sensor class: IUPAC has issued terminology and evaluation recommendations for electrochemical electronic tongue arrays. No comparable proposal yet exists for the fluorescence-based, PCA/HCA-driven discrimination claims that now dominate the Ln-MOF literature, which is the gap this paper addresses.

Adoption of each of the above guidelines was gradual and uneven, but the checklists gave editors and reviewers a concrete reference point to point to, rather than relying on individual judgment about what sufficient validation meant, and citation of the standard became, in itself, a signal that a study had been held to a defined bar. The parallel to fluorescence sensor arrays is not exact, since these earlier standards addressed measurement technologies used across thousands of laboratories, while Ln-MOF sensor arrays remain a smaller and more heterogeneous field. But the underlying problem, a fast-growing body of work converging on one analytical workflow without converging on what evidence that workflow requires, is close enough that the same style of solution is worth attempting early, before the reporting habits described in Sections 2 and 3 become any more entrenched.

The checklist proposed in Section 4 is deliberately modest in what it asks. Two of its nine items, a quantitative separation metric and a clear separation of classification from quantification claims, require no new experiments in the large majority of cases, only a different treatment of data a study has already collected. A further two or three items, blind sample testing and noise-robustness checks in particular, require additional effort but not additional material synthesis, and both have already been demonstrated as low-cost additions in the studies audited here [1][3][5]. The remaining items, concentration-range testing and real-matrix validation, are frequently already partially present in the titration and recovery data most studies generate for other purposes, and mainly require that the same data be re-examined through the lens of the discrimination claim rather than only the calibration claim.

Two audiences can act on this without waiting for a formal standard to be published. Reviewers can begin by requesting item 1 and item 6 as a routine condition of acceptance for any manuscript that claims multi-analyte discrimination, since both are inexpensive to satisfy and directly address the two gaps that recur most often in the literature surveyed here. Editors can support this by treating a quantitative separation metric as an expected component of a discrimination claim in reviewer guidelines, in the same way that a limit of detection is already an expected component of a sensitivity claim. Neither step requires community-wide consensus before it can start; either could be applied to the next submission a given journal receives.

The broader aim of this checklist is not to slow the field down. Ln-MOF sensor arrays have moved, within a few years, from single-analyte turn-on and turn-off probes to genuinely multiplexed platforms capable of resolving structurally similar antibiotics, dyes, and metabolites in real food and biological matrices, a capability that conventional chromatographic methods cannot match on cost, speed, or portability. That progress deserves an evidentiary standard that keeps pace with it. The gap this paper has described is not a shortage of good chemistry. It is a shortage of shared agreement about what, beyond a separated cluster on a plot, counts as proof that the chemistry works.

https://zenodo.org/records/21854123