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Circular Reference Standards in Deep-Learning Detection of Peri-Implant Bone Loss: A Methodological Analysis

Paper type
Methodological Study (theoretical)
Status
Original Work · Working Paper
Keywords:
peri-implantitis · deep learning · reference standard · incorporation bias · diagnostic accuracy · external validation · marginal bone loss
Contents
  1. 1Introduction
  2. 2Background and critical appraisal of the evidence
  3. 3Hypothesis and theoretical framework
  4. 4Proposed methodology
  5. 5Competing explanations and how the design discriminates among them
  6. 6Clinical and engineering implications
  7. 7Limitations
  8. 8Conclusions

Abstract

Background. Deep-learning models for peri-implant marginal bone loss and peri-implantitis report high performance. In most studies the reference standard is a clinician’s reading of the same radiograph that the model analyzes, whereas the disease is defined clinically by bleeding or suppuration, probing depth, and bone loss relative to a baseline radiograph.

Objective and hypothesis. To formalize how an image-derived reference standard (incorporation bias) relates apparent accuracy to accuracy for the clinical target, and to specify a validation design that identifies the gap. We hypothesize that when model and annotator errors are strongly correlated, apparent sensitivity and specificity approach 1 while accuracy for clinical disease stays near the annotators’ own accuracy, which a single radiograph limits because non-disease bone-level offsets (remodeling, placement depth) are indistinguishable from progressive loss.

Proposed approach. We derive apparent sensitivity and specificity as functions of disease prevalence, the sensitivity and specificity of model and annotator for the clinical target, and their conditional covariances, and prove a bound linking agreement to true accuracy. An illustrative simulation (run for this paper; not empirical data) and a closed-form grid quantify the gap. We then propose a blinded external validation on unselected consecutive implants with an independent clinical reference, sample-size reasoning for sensitivity and calibration, and a reporting checklist aligned with QUADAS-2/-3, QUADAS-AI, STARD-AI, TRIPOD+AI, and PROBAST+AI.

Expected contribution. The critique of image-derived references is already published for AI in apical periodontitis, and reviews of peri-implant AI document heterogeneous references and absent external validation. The contribution here is implant-specific: a formal bound, a construct-level explanation, a quantified illustration, and an executable design.

Conclusions. Under stated assumptions, agreement with annotators is nearly uninformative about accuracy for peri-implantitis. Claims of diagnostic accuracy should be restricted to “agreement with annotators on visible radiographic features” until a clinically referenced external validation exists.

1. Introduction

Peri-implantitis is a clinical diagnosis. The 2017 World Workshop consensus describes it through bleeding and/or suppuration on gentle probing, increased probing depth, and radiographic bone loss beyond initial remodeling [1]. The epidemiology of the condition is sensitive to the case definition used [2]. Radiographic bone level is one component of that definition, and in the absence of a baseline image it is an ambiguous component, because an implant placed deeper, or one that remodeled normally in the first year, shows the same bone level in a single film as an implant that has lost bone through disease.

Deep-learning models are now being built for this task. Recent syntheses describe high technical performance: a meta-analysis of five studies and 12,545 periapical and panoramic radiographs reported pooled sensitivity of 88%, specificity of 91%, and an area under the curve of 0.95, while stating that such models cannot substitute for clinical assessment [3]. A later review of 17 studies reported implant detection and segmentation metrics near 0.98 but a lower precision, about 0.78, for downstream peri-implantitis classification [4]. These numbers are usually read as the accuracy of the model for peri-implant disease. This paper argues that the study designs behind them mostly cannot support that reading.

The argument is simple. If the reference label is produced by a clinician looking at the same radiograph that the model analyzes, the label is a function of the index image. The model is trained to reproduce that function. High agreement then measures how well the model has learned the annotators’ reading of visible features. It does not measure how often the model agrees with the disease. The gap between the two depends on how well annotators themselves identify clinical disease from the image, and on how strongly the model’s errors track the annotators’ errors.

We do not claim that this observation is new in the broader literature. Incorporation of the index test into the reference standard is a long-recognized source of bias in diagnostic accuracy research [5, 6], and the consequences of dependent errors between a test and an imperfect reference have been derived formally [7]. Dental AI has already received an explicit version of the critique for apical periodontitis, where most primary studies used a label that was a reading of the index image [8]. What is missing for implants is a formal treatment tied to the peri-implantitis construct, a quantified illustration, and a design that would measure the gap. The paper supplies these, and it states throughout which of its statements are derivations, which are assumptions, and which are predictions awaiting data.

No clinical or imaging data were analyzed. The only computation is a Monte Carlo and closed-form illustration with assumed parameters (Section 3.7). Evidence appraisal was done on abstracts only.

2. Background and critical appraisal of the evidence

Origin of the concept

Ransohoff and Feinstein described how the spectrum of patients and the way the reference is assembled can distort the apparent efficacy of a diagnostic test [5]. The systematic review of sources of variation and bias by Whiting and colleagues listed incorporation of the index test into the reference standard among them [6], and the QUADAS-2 tool carries a reference-standard domain among its four domains [9]. The QUADAS-3 revision and the AI-specific QUADAS-AI extension continue this line [10, 11]. A general statistical literature treats the case where no gold standard exists: latent class models with explicit conditional dependence between tests [12, 13], simulation work on when such models recover sensitivity and specificity [14, 15], and work showing that conditional dependence can arise from shared covariates [16]. A recent paper uses directed acyclic graphs to show how common biases in diagnostic accuracy studies arise [17].

The result most relevant here is Walter and colleagues’ derivation of apparent sensitivity, specificity, and accuracy of a test against an imperfect reference whose errors may be dependent on the test’s errors [7]. They show that either positive or negative bias can occur, and that its sign and size depend on prevalence, the true accuracies, and the covariances of the false-negative and false-positive errors. Two points follow for this paper. First, dependence raises agreement between the test and the reference, but the effect on apparent accuracy is not always an inflation. Second, we should not assert that the apparent accuracy of an implant model is inflated unless we state the dependence assumptions under which it is.

What the peri-implant AI literature reports

Table 1 summarizes the pivotal syntheses and primary studies. The summaries reflect abstracts only.

Table 1. Pivotal sources on AI for peri-implant bone loss and related methodological literature, with operational evidence level.
SourceDesign and sizeFinding relevant hereMain limitationLevel
Atieh 2026 [3]Meta-analysis, 5 studies, 12,545 radiographsPooled Se 88%, Sp 91%, AUC 0.95; dataset size and unit of analysis influenced accuracy; no publication bias detectedPooling over heterogeneous references; abstract does not state reference independenceB
Khanzadeh 2026 [4]Systematic review, 17 studies, QUADAS-3 and PROBASTDetection F1 0.984, segmentation Dice 0.986, peri-implantitis classification precision 0.777; six studies used independent multi-rater references; none had independent multicenter external validation; data often enriched or internally splitReviews reference quality but gives no formal modelB
Patil 2026 [18]Systematic review, 8 retrospective single-center studiesHigh risk of bias in patient selection and index test; internal validation only; certainty very low; only two studies allowed derivation of Se and SpFew studies; QUADAS-2B
Mugri 2025 [19]Systematic review, 7 studiesReference defined as expert opinion; all studies rated low risk of biasRating at odds with the other reviewsC
Fanelli 2026 [20]Review, 10 studiesHeterogeneous reference standards, retrospective, internal validation onlyNarrative synthesisC
Adnan 2026 [21]Development study, 2,960 radiographs; 40 radiograph pairs for measurement comparisonModels applied to sequential radiographs; compared with a specialist-established referenceReference is image-based; small comparison setC
Alkhattab and Bokhary 2026 [8]Narrative review, apical periodontitis, 44 primary studies34 used a label that was a reading of the index image or was unascertainable; 8 used an independent reference; same-image vs blinded CBCT sensitivity differed markedly for one platformDifferent disease; narrative reviewC
Walter 2012 [7]Statistical derivationApparent accuracy against an imperfect reference with dependent errors can be biased in either directionNot applied to dentistryD
Zhu 2025 [22]Systematic review, implant outcome prediction modelsFew of the 43 models externally validated; calibration rarely reportedPrediction of failure, not image detectionB

Evidence levels A to E are operational categories used in this paper (A strong, B moderate, C preliminary, D mechanistic or theoretical, E speculative hypothesis); they are not GRADE ratings.

First, the syntheses disagree on quality. Atieh and colleagues rated quality as generally good [3] and Mugri rated all seven included studies as low risk of bias [19], whereas Patil and colleagues found high risk in patient selection and index-test domains and judged certainty very low [18]. The contradiction is partly explained by what each review counted as the reference standard: when the reference is defined as “expert opinion on radiographs,” a risk-of-bias tool that asks whether the reference is applied consistently can be satisfied even though the reference is not independent of the index image. This is our interpretation, not a statement made in those abstracts.

Second, the most recent reviews already note that references are heterogeneous and that external validation is lacking [4, 18, 20]. The review by Khanzadeh and colleagues goes a step further by counting studies that used explicitly independent multi-rater references [4]. Independence among raters is not independence from the image, however: a multi-rater consensus on a radiograph is still a function of that radiograph. A reference can be independent of the model’s developers and still be incorporated with respect to the index image. We therefore distinguish three kinds of independence in Section 3.1.

Third, the same critique exists for a neighboring disease. The apical periodontitis review reports that most primary studies used a label that was a reading of the index image, and that for one commercial platform sensitivity differed substantially between a same-image consensus and a blinded CBCT reference [8]. That review also notes that for real-world models the direction of the bias depends on error dependence that the study design cannot identify [8]. We adopt this caution. It means that the correct claim for implant AI is a conditional one, with the conditions made explicit, and not the unconditional claim that reported accuracy is inflated.

What is not known

We found no study in the abstracts retrieved that reports sensitivity and specificity of a peri-implant deep-learning model against a blinded clinical reference (bleeding, suppuration, probing depth) with a baseline radiograph, on unselected consecutive implants, in a validation sample separate from development. This statement is limited by abstract-level appraisal and by the inability to search Embase, Scopus, or Web of Science; the Patil review reports using Scopus and Embase-indexed records [18], so its coverage partly compensates. We also found no estimate of how accurately annotators identify clinical peri-implantitis from a single radiograph, which is the central unknown in the framework below. Cross-center generalization has been shown to fail for a dental radiograph model in a different task: performance fell when the model was applied to data from another center [23]. This supports the need for external validation but is not evidence about peri-implant reference standards.

The prediction-model literature adds a related gap: few of 43 implant outcome models were externally validated, and calibration is rarely reported [22]. Reporting and risk-of-bias tools exist [24, 25], as does an updated imaging checklist [26]; Section 4.8 returns to them.

3. Hypothesis and theoretical framework

Three kinds of independence

A reference standard can be independent of the model’s training process, independent of the raters’ prior knowledge, or independent of the index image. Most of what reviews call independent multi-rater consensus achieves the first or second. Only the third removes incorporation of the index image into the reference. We call a reference image-derived if it is a function of the index radiograph, image-augmented if it is a function of the index radiograph plus other information that is not itself clinical examination (for example, a second radiograph), and clinically independent if it is obtained by examination of the patient, blinded to the model output, with the radiographic component defined relative to a baseline image. The terms are working definitions for this paper.

Notation

The unit of analysis is an implant at a defined examination time. Let D denote the clinical target, D = 1 for peri-implantitis under a stated case definition and D = 0 otherwise, with prevalence π=P(D=1) in the validation population. Let R be the binary label produced by annotators reading the index radiograph, and M the binary model output at a fixed operating threshold. Define the accuracies of model and annotators for the clinical target:

Se_M=P(M=1∣D=1), Sp_M=P(M=0∣D=0), Se_R=P(R=1∣D=1), Sp_R=P(R=0∣D=0).

Define the conditional covariances of the two classifiers within each disease stratum, c_1=Cov(M,R∣D=1) and c_0=Cov(M,R∣D=0), and the corresponding correlations

ρ_1=c_1/(√(Se_M(1−Se_M) Se_R(1−Se_R))),  ρ_0=c_0/(√(Sp_M(1−Sp_M) Sp_R(1−Sp_R))).

All quantities are dimensionless proportions. The correlations are bounded by the Fréchet limits implied by the marginals.

Apparent accuracy against an image-derived reference

When R is treated as the reference, the apparent sensitivity and specificity are Se_(app)=P(M=1∣R=1) and Sp_(app)=P(M=0∣R=0). Writing the joint probabilities in terms of the stratum-specific marginals and covariances gives

P(M=1,R=1)=π (Se_MSe_R+c_1)+(1−π) ((1−Sp_M)(1−Sp_R)+c_0),

P(R=1)=π Se_R+(1−π)(1−Sp_R),

Se_(app)=(P(M=1,R=1))/(P(R=1)),  Sp_(app)=(π ((1−Se_M)(1−Se_R)+c_1)+(1−π) (Sp_MSp_R+c_0))/(1−P(R=1)).

These expressions are an instance of the general result of Walter and colleagues for dependent errors against an imperfect reference [7], written with the notation of this paper. The latent class literature uses the same structure to estimate accuracies when dependence parameters are modeled [12, 16].

Proposition 1 (agreement bound). Let δ_1=P(M≠R∣D=1) and δ_0=P(M≠R∣D=0). Then (Se_M−Se_R)≤δ_1 and (Sp_M−Sp_R)≤δ_0, and overall agreement is A=1−πδ_1−(1−π)δ_0.

Argument. (P(M=1∣D=1)−P(R=1∣D=1))≤P(M≠R∣D=1), because the two probabilities can differ only on the event that the labels differ. The same holds in the stratum D=0. The expression for A follows by total probability. ▫

The proposition says that the accuracy of the model for the clinical target is pinned to the annotators’ own accuracy to within the disagreement rate. If agreement is high, δ_1 and δ_0 are small and the model’s true sensitivity and specificity are close to those of the annotators, whatever the annotators’ accuracy is. At low prevalence the bound on δ_1 is weaker, since δ_1≤(1−A)/π, so high overall agreement does not by itself confine sensitivity.

Corollary 1. If the model reproduces the annotators exactly (M = R), then Se_(app)=Sp_(app)=A=1 while Se_M=Se_R and Sp_M=Sp_R. Apparent accuracy is then uninformative about accuracy for D beyond what is known about the annotators.

Corollary 2 (the model is penalized for being right). Suppose the model is more accurate than the annotators for D but its errors are independent of theirs (c_1=c_0=0). Apparent sensitivity and specificity then understate the model’s true values, because every case where the model is correct and the annotator is wrong counts as a model error. Accuracy gains beyond the annotator therefore cannot be shown against an image-derived reference; they are invisible or negative.

The two corollaries show why the direction of bias is not fixed [7, 8]. For models trained to reproduce annotator labels, which is the usual procedure, correlation is expected to be high. We therefore treat high ρ_1 and ρ_0 as a plausible but untested assumption (A3 below), and not as a fact.

Why a single radiograph limits accuracy for D

Let X be the information in the index radiograph. Both M and R are functions of X plus noise. For any classifier that is a function of X, the attainable pairs (Se,Sp) for D lie on or below the receiver operating curve of the likelihood ratio P(X∣D=1)/P(X∣D=0); no model trained on X can do better than the information in X allows, regardless of the labels it is trained on. If the visible bone level is the sum of a non-disease offset (remodeling, placement depth, prior surgery) and progressive loss, the single-image distributions for D = 1 and D = 0 overlap, and the ceiling is below 1. Agreement with annotators can still be near 1, because annotators are subject to the same ceiling and the model is learning their rule. The clinical definition addresses this overlap by using a baseline radiograph and clinical signs [1]; a model given the baseline image would face a different, less overlapping problem.

Assumptions

  • A1. The clinical target D is well defined and measured without error in the validation study. In practice, bleeding on probing and probing depth are themselves variable. Section 4.6 treats this as a sensitivity analysis.
  • A2. R is a function of the index radiograph and does not use clinical information.
  • A3. The model was trained, in whole or part, on labels of the same kind as R, so that ρ_1 and ρ_0 are positive and may be large.
  • A4. A non-disease component of bone level (offset) varies between implants and is not separable from progressive loss in a single image.
  • A5. Accuracy parameters are transportable to the validation population; spectrum differences are handled by the sampling design.

Hypothesis and predictions

Hypothesis H1. Under A1 to A5, in an unselected cohort of implants, the apparent accuracy of a model trained on annotator labels and evaluated against annotator labels will exceed its accuracy against an independent clinical reference by a margin that grows with ρ_1, ρ_0 and with the variance of the non-disease offset.

Predictions:

  • P1. The AUC of the model against the clinical reference is lower than its AUC against annotator labels in the same implants by at least 0.05. It would be refuted if the difference is below 0.02 with a confidence interval excluding 0.05, or if the AUC against the clinical reference remains at or above 0.90 (the falsification criterion we adopt, taken from the candidate notes for this paper).
  • P2. The model’s sensitivity and specificity for the clinical reference are within δ_1 and δ_0 of the annotators’ own values (Proposition 1, which is mathematical and cannot be refuted, but whose assumed premise, that the model was trained on annotator labels, can).
  • P3. A model given baseline and follow-up radiographs has higher accuracy for the clinical reference than a single-image model, with agreement against single-image annotators unchanged or lower. This discriminates an information deficit from a model deficit. It is refuted if baseline access does not improve accuracy.
  • P4. The gap increases with the variance of the non-disease offset (for example, in cohorts with mixed placement depths or platform designs).
  • P5. The gap decreases when annotators are more accurate for D, for example when annotators are given the clinical chart. This would also show that the gap is a reference property and not a model property.
  • P6. Calibration against the clinical reference is worse than calibration against annotator labels (calibration slope below 1 or intercept shifted), because the model’s scores encode the annotators’ prevalence of labelled disease, not clinical prevalence.

Illustrative computation under stated assumptions — not empirical data

The script sim.py in the paper folder was run for this paper. It does two things.

Monte Carlo. Prevalence of clinical disease was set at 0.20. For each implant, a non-disease bone-level offset r was drawn from a normal distribution (mean 1.5 mm, SD 0.8 mm, truncated at 0). For D = 1, progressive loss L was drawn from a normal distribution (mean 1.6 mm, SD 1.0 mm, truncated at 0.05 mm); for D = 0, L = 0. The visible bone level is x = r + L. The annotator label was R = 1 if x plus noise (SD 0.35 mm) exceeded 3.0 mm. The model saw x plus independent noise (SD 0.35 mm), and was a one-feature logistic regression fitted to the annotator labels in a training set of 20,000 implants, then evaluated on 400,000 new implants. A baseline-aware comparator used the difference between the follow-up bone level and the baseline offset (measured with noise SD 0.35 mm) at a 0.8 mm cut-off. The random seed was 20261117. These parameters are assumptions chosen to represent overlap between remodeling and disease; they are not estimates from patients.

In the base scenario the model agreed with the annotators on 94.6% of implants (kappa 0.767), with apparent sensitivity 0.750, apparent specificity 0.979, and an AUC of 0.976 against the annotator label. Against the simulated clinical truth the same model had sensitivity 0.496, specificity 0.968, positive predictive value 0.796, and AUC 0.854. The annotators themselves had sensitivity 0.533 and specificity 0.957 for D, which is consistent with Proposition 1: the model’s true accuracy was close to theirs. The baseline-aware comparator had sensitivity 0.777, specificity 0.989, and AUC 0.940. The reconstruction of apparent sensitivity and specificity from the closed-form equation using the simulated covariances (c_1 = 0.189, c_0 = 0.018) gave 0.7503 and 0.9785, matching the simulated values (0.7503 and 0.9785), which checks the algebra of Section 3.3.

Table 2. Illustrative simulation under stated assumptions (not empirical data): agreement with annotators versus accuracy for simulated clinical disease. Each row changes the stated parameter from the base scenario; rows are from a separate random draw, so base-row values differ slightly from the text.
ScenarioAgreement with RSe (apparent)Sp (apparent)AUC vs RSe (vs D)Sp (vs D)AUC vs D
Base0.9460.7430.9790.9760.4910.9700.854
Annotator and model noise SD 0.15 mm0.9770.9000.9890.9960.5250.9700.864
Annotator and model noise SD 0.60 mm0.9010.5480.9690.9160.4340.9670.831
Offset SD 0.4 mm0.9680.8220.9860.9890.5040.9990.912
Offset SD 1.2 mm0.9320.7890.9670.9750.5080.8980.803
Mean disease loss 2.5 mm0.9510.8380.9780.9840.7530.9670.945
Prevalence 0.100.9550.6470.9860.9720.4780.9720.854

Closed-form grid. With π = 0.20, Se_M=Se_R = 0.75, Sp_M=Sp_R = 0.90 and ρ_1=ρ_0=ρ, the apparent values were as follows. At ρ = 0: Se_(app) 0.524, Sp_(app) 0.858, agreement 0.781. At ρ = 0.5: 0.762, 0.929, 0.891. At ρ = 0.75: 0.881, 0.964, 0.945. At ρ = 0.9: 0.952, 0.986, 0.978. At ρ = 1: 1, 1, 1. The true values were 0.75 and 0.90 throughout. The grid shows the sign problem in Corollary 2: with independent errors, apparent sensitivity (0.524) is below the true value; at moderate correlation the two nearly coincide (0.762 against 0.75); only at high correlation does the apparent value exceed the truth substantially.

What the computation shows and does not show. In the simulation, the annotator’s own sensitivity for D is about 0.53 because many diseased implants have visible bone loss that is within the range of non-disease offsets. This outcome follows from parameters we chose; it is not a finding about annotators. In the “offset SD 0.4 mm” row, where the overlap is smaller, the AUC against D rises to 0.912; in the “mean disease loss 2.5 mm” row, true sensitivity rises to 0.753. The computation supports a conditional statement: if annotators miss disease that is not visible on a single image, high agreement and a high AUC against annotators can coexist with much lower accuracy for the clinical target. Whether real annotators behave this way is the empirical question Section 4 addresses.

4. Proposed methodology

The design below is a proposal. No part of it has been carried out, and no ethics approval or registration exists.

Design

A prospective or ambispective diagnostic accuracy study of a frozen (locked) deep-learning model, evaluated in a validation cohort that is separate from model development in time, place, and patients. The index test is the model applied to the radiographs. Three comparisons are made on the same implants: (i) model output against annotator labels of the index radiograph (the apparent estimate); (ii) model output against an independent clinical reference (the estimate of interest); and (iii) annotators against the clinical reference (the benchmark and the key unknown, Se_R and Sp_R). The difference between (i) and (ii) is the incorporation gap. Figure 2 summarizes the design.

Population and sampling

Consecutive patients with at least one functioning implant, loaded for at least one year and with a retrievable baseline radiograph (for example, at prosthesis delivery), attending maintenance or recall visits at two or more centers not used in model development. Sampling must not be enriched by radiographic appearance or by referral for suspected disease; enrichment changes prevalence and the spectrum of non-disease bone levels, and the reviews we appraised noted enriched or internally split datasets [4]. Exclusions are limited to implants with no readable radiograph or no clinical examination within the window. The unit of analysis is the implant, with clustering by patient. Several development studies used datasets of several hundred to a few thousand images, for example 708 periapical radiographs in one measurement study and 800 in a severity-classification study [27, 28], and one recent cascade used 2,960 radiographs [21]; a validation cohort of the size in Section 4.5 is therefore larger than most development sets.

Index test and comparators

The model is frozen before the validation cohort is assembled, with operating threshold fixed in advance. Three versions are evaluated when available: a single-image model, a model given baseline and follow-up radiographs, and any commercial or published model the investigators can run. The annotator comparator consists of two or more clinicians reading the index radiograph only, blinded to the clinical examination, with disagreement resolved by a third reader. A second annotator condition, in which clinicians receive the clinical chart, is included to test P5. The model must not be trained on any radiograph from validation patients, and patient identifiers must be used to audit image-level leakage between development and validation sets.

Independent clinical reference

The reference is a clinical examination within a short window (for example, four weeks) of the index radiograph, by an examiner blinded to the model and to radiographic labels. The case definition follows the 2017 consensus: bleeding and/or suppuration on gentle probing, probing depth increase relative to a prior record where available, and radiographic bone loss beyond initial remodeling assessed against the baseline radiograph [1]. Because the definition is multi-component, the study pre-specifies a primary composite and reports each component separately. Probing and bleeding procedures are standardized (probe type, force, number of sites) and examiners are calibrated, with repeat examination in a subsample to estimate reference reliability. The bone-level component uses standardized radiographs with a calibration object and a documented projection method; non-standardized projection adds measurement error to both sides of the comparison and is recorded as a covariate.

Note that the bone-loss component of this reference still uses a radiograph. It uses a baseline radiograph, which changes the quantity being measured from absolute bone level to bone-level change, and it is combined with clinical signs that the index image cannot contain. The reference is therefore clinically independent in the sense of Section 3.1, but not free of radiographic input. This residual dependence is addressed in Section 5.

Outcomes and sample-size reasoning

Primary outcomes are sensitivity and specificity of the model at its fixed threshold against the clinical reference. Secondary outcomes are AUC, positive and negative predictive values, calibration of any probability output, the incorporation gap (apparent minus clinical-reference estimates), and the annotators’ Se_R and Sp_R.

The sample size for estimating sensitivity with a confidence-interval half-width d at confidence level 95% follows the prevalence-adjusted approach of Buderer [29]:

n_(D+)=(z^2 Se (1−Se))/(d^2),  n=(n_(D+))/π×DE,  DE=1+(m−1) ICC,

with z=1.96, prevalence π, mean implants per patient m, and intraclass correlation ICC. The corresponding specificity requirement uses n_(D−)=z^2Sp(1−Sp)/d^2 divided by (1−π). We assumed m=1.6 and ICC=0.5, giving DE=1.30; these values are placeholders to be replaced by pilot estimates. The calculation was run in the script sim.py and produced the following numbers (implants unless stated).

Scenario a. Expected Se=0.80, Sp=0.85, d=0.05, π=0.20: 1,230 implants for sensitivity (246 with disease) and 245 for specificity. Sensitivity is binding. With the design effect, 1,599 implants, approximately 999 patients.

Scenario b. The same, with π=0.10: 2,459 implants for sensitivity, 218 for specificity; 3,197 implants after the design effect, approximately 1,998 patients.

Scenario c. The same as scenario a with d=0.07: 628 implants, 816 after the design effect, approximately 510 patients.

Scenario d. Se=Sp=0.90, d=0.05, π=0.20: 692 implants, 899 after the design effect, approximately 562 patients.

The sensitivity requirement dominates whenever disease prevalence is low, which is why unselected sampling is expensive and why enriched sampling is tempting. The study should be sized on the number of reference-positive implants (about 246 in scenario a). The incorporation gap is estimated on the same implants and its estimator is paired, so its variance is expected to be smaller than the sum of the variances of the two estimates; the exact variance depends on the covariances in Section 3.2, and a bootstrap simulation using pilot data should be run before finalizing the sample size.

For models that output probabilities, the sample size should also satisfy criteria for precision of calibration and of the net benefit, such as those developed for external validation of prediction models with a binary outcome [30]. As a simple check we computed the approximate precision of the observed-to-expected ratio from SE(lnO/E)≈√((1−φ)/(nφ)) for outcome proportion φ. For φ=0.20 the 95% interval is about a factor of 1.13 either way at n=1,000 and 1.11 at n=1,500; for φ=0.10 the factors are 1.20 at 1,000 and 1.16 at 1,500. This approximation is our own calculation and its relation to the criteria in [30] must be checked against the full text.

Statistical analysis plan

Primary analysis. Sensitivity and specificity against the clinical reference with 95% confidence intervals from a patient-level cluster bootstrap. The same estimates against annotator labels. The gap is the paired difference, with a bootstrap interval. The pre-specified hypothesis test for P1 is whether the lower bound of the confidence interval for the AUC difference exceeds 0.02, and whether the point estimate of AUC against the clinical reference is below 0.90.

Calibration. For probability outputs, calibration intercept and slope, calibration plot with smoothing, and observed-to-expected ratio, each against the clinical reference. Decision-curve analysis is exploratory; it requires a defined clinical action, such as referral for clinical probing, which the investigators must specify. Models that are not designed to give probabilities should be reported as such rather than recalibrated post hoc.

Dependence. Estimate c_1, c_0, ρ_1 and ρ_0 directly, since all three labels are observed in the validation sample. Show the closed-form decomposition of Section 3.3 so that readers can see how much of the gap is attributable to annotator error and how much to model–annotator dependence.

Imperfect clinical reference. Bleeding on probing and probing depth are variable. Sensitivity analyses use latent class models with explicit conditional dependence [12, 16], informed priors for the reference’s sensitivity and specificity from the repeat-examination subsample, and checks for violations of conditional independence [15]. Latent class estimates are not identified without constraints [13, 14]; they are presented as sensitivity analyses and not as the primary result. Bayesian methods that adjust jointly for verification and reference-standard bias exist [31] and are relevant if only radiographically suspicious implants receive a full clinical examination.

Missing and partially verified data. If clinical examination is not done on all implants, a verification-bias analysis is required; the design in Section 4.2 aims to avoid it by examining all consecutive implants.

Subgroups. Center, implant system, imaging type, projection quality, and baseline-image availability are exploratory interaction analyses.

Bias control

Blinding: the clinical examiner does not see radiographic labels or model output; annotators do not see the chart (except in the P5 arm); the model sees only images. Timing: the examination and the follow-up radiograph fall within the same pre-specified window. Spectrum: consecutive sampling and reporting of the distribution of baseline bone levels and of non-disease bone-level offsets. Leakage: patient-level separation between development and validation, with the audit in Section 4.3. Threshold: fixed before the validation data are opened. Unreadable images are reported with the denominator retained.

Reporting checklist aligned with existing tools

The tools we cite were verified in PubMed as published papers: QUADAS-2 [9] with its revision QUADAS-3 [10] and AI extension QUADAS-AI [11]; STARD-AI [32]; TRIPOD+AI [24]; PROBAST+AI [25]; and CLAIM [26]. We appraised abstracts only, so Table 3 links each checklist item to the domain of the tool at the level of domain names and does not reproduce item numbers or wording, which must be taken from the full publications.

Table 3. Reporting checklist for AI studies of peri-implant bone loss and peri-implantitis, mapped to existing tools at domain level.
Item to reportSpecific requirement for this fieldRelated tool domain
Target conditionCase definition of peri-implantitis and of the radiographic component (absolute level or change from baseline)Reference standard (QUADAS-2/3/AI; STARD-AI)
Reference standardHow it was produced; whether it is a function of the index image; examiner blinding; reliabilityReference standard (QUADAS-2/3/AI; STARD-AI; PROBAST+AI)
Independence statementWhich of the three independences in Section 3.1 applyReference standard; applicability
Participants and samplingConsecutive or enriched; prevalence; patients and implants; source centersPatient selection (QUADAS-2/3/AI); STARD-AI; TRIPOD+AI
Data partitioningPatient-level split; external or internal; leakage auditIndex test; analysis (PROBAST+AI; TRIPOD+AI; CLAIM)
Index testModel version, input (single image or baseline pair), threshold fixed in advanceIndex test (QUADAS-2/3/AI); CLAIM
AnnotatorsNumber, experience, blinding, consensus rule, agreement statisticsReference standard; CLAIM
PerformanceSe, Sp, PPV, NPV, AUC with confidence intervals against both reference types; gap; c1, c0STARD-AI; TRIPOD+AI
CalibrationSlope, intercept, O/E, plot, for probability outputsTRIPOD+AI; PROBAST+AI analysis domain
Clinical useIntended use, comparator workflow, harms of misclassificationSTARD-AI; TRIPOD+AI

Ethics and feasibility

A study of this kind needs ethics approval and informed consent; none has been sought. Clinical examination is routine in maintenance care, so the incremental burden is standardization and calibration; the main constraints are baseline radiographs and blinded examiners. A multicenter practice network is the likely route to the sample sizes in Section 4.5. ClinicalTrials.gov lists a not-yet-recruiting observational study on large language models and panoramic marginal bone loss, but we did not read its protocol and do not know its reference standard.

5. Competing explanations and how the design discriminates among them

Explanation 1: annotators are accurate for D, so no gap exists. If Se_R and Sp_R against the clinical reference are high, then by Proposition 1 the model’s true accuracy is also high. The design measures Se_R and Sp_R directly. Observing a high value would refute H1 for that setting.

Explanation 2: errors are independent, so apparent accuracy is biased downward. Corollary 2 and the ρ=0 row of the grid show this case. The direct estimates of c_1 and c_0 in the validation sample discriminate it from the dependent-error case; the incorporation gap would then have the opposite sign to the one hypothesized, which is a refutation of the direction in H1.

Explanation 3: the gap arises from spectrum or enrichment, not from the reference. Development studies often use selected or enriched data [4]. Because the same implants are evaluated against both references, a spectrum effect applies to both and cancels in the paired gap, whereas the absolute estimates change. Comparing enriched and unselected subsets of the validation cohort separates the two.

Explanation 4: the single image is uninformative, and the problem is information and not the reference. This is the mechanism in Section 3.4, and it is not an alternative to H1 but a part of it. P3 and P5 distinguish an information deficit (baseline images or clinical data close the gap) from annotator noise (which they would not).

Explanation 5: the clinical reference is itself noisy, so the measured gap is partly reference error. Reference error biases accuracy against the clinical reference in a direction that depends on its own errors; this is the general problem of imperfect reference standards [7]. Repeat examinations, latent class sensitivity analyses, and a pre-specified component-by-component report address it. If the reference’s reliability is low, the study can support only a narrower statement, namely that the model’s agreement with a clinical composite is lower than its agreement with annotators.

Explanation 6: image-level leakage inflates apparent internal accuracy. A separate mechanism that also yields high apparent accuracy. A leakage audit and a patient-level split separate it from incorporation bias; the incorporation gap persists in a leak-free external sample, whereas leakage-driven inflation vanishes there.

6. Clinical and engineering implications

These implications are conditional on the hypothesis being supported by a clinically referenced validation.

Interpretation of existing claims. Until such validation exists, reported performance of peri-implant models is best described as agreement with annotators on visible radiographic features. The phrase “diagnostic accuracy for peri-implantitis” would be justified only for models evaluated against a clinical reference. This wording matches the cautious conclusions of the reviews, which call the evidence investigational or insufficient for routine use [4, 18], and the statement in the meta-analysis that models cannot replace clinical assessment [3]. It also follows from the broader pattern in implant AI of high headline accuracy with heterogeneous designs: a review of radiograph-based implant prognosis models reported accuracy as high as 99.8% across 13 heterogeneous studies [33], and a review of implant classification and peri-implant pathology identification rated the majority of studies as high or unclear risk of bias on a QUADAS-2 assessment [34]. A meta-analysis of implant-system identification noted high risk of bias and applicability concerns for most studies, including in the reference-standard domain [35]. These reviews concern different tasks, and the reference-standard problem differs by task: for implant-system identification the label is a manufacturer record, which is a far less circular reference than annotation of bone loss.

Use as a measurement aid. Where the task is measurement of bone level on a standardized radiograph, agreement with expert measurement is a legitimate target and the incorporation problem is less severe, since the quantity of interest is the radiographic distance itself. The problem arises when measurement is promoted to disease classification. A model that measures bone level accurately cannot, from a single image, say whether the level reflects disease or remodeling. A conditional recommendation follows: models should be presented as measurement or triage aids whose output requires clinical examination, and thresholds should be labeled as radiographic, not diagnostic.

Use of baseline images. If P3 holds, the more promising engineering direction is models that take paired baseline and follow-up radiographs, because the information deficit identified in Section 3.4 is addressed by the input and not by the architecture. One recent development study already frames its cascade around sequential radiographs and notes that single-time-point evaluation neglects baseline comparison [21]. That study compared its output with a specialist-established reference, so the incorporation concern remains for the reference.

Training labels. Training on labels derived from clinical outcomes would break the dependence between model and annotator errors by construction, at the cost of requiring longitudinal data.

Prediction models. For prediction models of implant failure or peri-implantitis, the analogous requirements are external validation and calibration. A multicenter gradient-boosting model for implant failure reported strong discrimination on a hold-out sample and checks of calibration [36]; however, our reading of its abstract suggests that its classes were roughly balanced, which, if true, would distort calibration relative to real-world failure rates. This is an inference from an abstract and is stated as such. It illustrates why calibration needs an unselected validation cohort even when external checks are reported.

7. Limitations

  • The central parameters are unknown. Se_R, Sp_R, ρ_1, and ρ_0 for peri-implant annotation have not been estimated by us or, to our knowledge from abstracts, by others. The simulation shows what follows from assumptions, not what is true.
  • The simulation is a one-dimensional caricature. Real radiographs carry texture, thread pattern, angulation, and soft-tissue information that could partly distinguish disease from remodeling, and deep models might use some of it. The single-feature model understates what a convolutional network could extract. If it extracts disease-specific signals that annotators do not use, then Corollary 2 applies and the true accuracy could exceed the annotators’.
  • Annotators may not be image-only. Some studies may have labeled radiographs with clinical records at hand; abstracts do not say, so A2 may fail.
  • The clinical reference is imperfect and partly radiographic. Section 4.4 and Explanation 5 address this, but they do not remove it.
  • Abstract-level appraisal. We read abstracts only. Several statements about which studies used which reference come from review abstracts and could be corrected by full texts. Embase, Scopus, and Web of Science were not accessible; Patil and colleagues reported searching Scopus and Embase-indexed records [18], and Khanzadeh and colleagues searched all three [4].
  • Novelty is limited. The core critique has an antecedent in AI for apical periodontitis [8], and the statistical result on dependent errors is established [7]. The incremental contribution is a specialization and a design.
  • Sample sizes are placeholders. The ICC, implants per patient, and expected accuracy are assumed. The approximation for the O/E ratio was computed here and has not been checked against the cited sample-size criteria.
  • Definition of peri-implantitis. Prevalence and the proportion of non-disease bone-level change both depend on the case definition and on the follow-up time since loading [2]. A study that uses a different case definition would measure a different gap.

8. Conclusions

Under the stated assumptions, a deep-learning model trained and evaluated against annotators of the same radiograph can show high agreement while its accuracy for clinically defined peri-implantitis is close to the annotators’ own, which a single image can bound well below 1. The apparent value is not always an overestimate: with independent errors it can be an underestimate. Peri-implant AI studies should state which kind of independence their reference has, report agreement and clinical accuracy separately, and move toward external validation on unselected cohorts with a blinded clinical reference and baseline radiographs. The central quantities remain to be measured.

Cite this paper

Jain S, Gupta A. Circular Reference Standards in Deep-Learning Detection of Peri-Implant Bone Loss: A Methodological Analysis. Working paper. Center for Implant Dentistry; 2026. Available from: https://bayareaimplantdentistry.com/clinician-research-and-publications/ai-bone-loss-circular-reference-standard

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