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Seeing Thin Bone: A Diagnostic Accuracy Protocol for Cone-Beam CT Assessment of Buccal Bone and Peri-Implant Defects Against an Intra-Surgical Reference Standard

Paper type
Study Protocol (diagnostic accuracy; STARD-oriented)
Status
Original Work · Working Paper
Keywords:
cone-beam computed tomography · dental implants · buccal bone · peri-implant dehiscence · diagnostic accuracy · metal artifact reduction · STARD
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. Clinical rules about buccal bone thickness at implants, such as the 1.5-2 mm rule, and CBCT-based follow-up of peri-implant bone presuppose that cone-beam computed tomography (CBCT) can see thin bone beside titanium or zirconia. Ex vivo and animal studies suggest that below about 1 mm true thickness it cannot reliably separate intact thin bone from dehiscence, and the one systematic review of peri-implant defect detection located only in vitro and animal evidence. We found no human study that validates CBCT against surgical findings at implants.

Objective and hypothesis. To specify a prospective diagnostic-accuracy study (STARD-oriented) that estimates CBCT sensitivity, specificity and thickness agreement against direct intra-surgical assessment. We hypothesize that accuracy for buccal bone breach falls with decreasing wall thickness, that sensitivity and specificity do not both reach 80% in the thin-wall stratum, and that metal-artifact reduction (MAR) does not change this.

Proposed approach. Adults already scheduled for flap surgery at an implant, in whom CBCT is independently indicated, would be imaged without any research-only exposure. Blinded readers would classify breach status and measure wall-edge thickness, with MAR on and off reconstructed from the same raw data. The reference standard is calibrated direct measurement with an intra-operative surface scan, assessed blind to CBCT. Under stated assumptions (sensitivity 0.70, specificity 0.75, 95% confidence half-width 0.10, assumed 35% site-level prevalence, three sites per patient, intracluster correlation 0.30), about 372 sites in 124 patients are needed, or 146 allowing 15% loss. Analysis uses clustered ROC and logistic methods, Bland-Altman limits of agreement, and prespecified subgroups (titanium versus zirconia, MAR, voxel size).

Expected contribution. The study would supply the missing human in vivo validation, or show that the ex vivo failure does not transfer to patients. Either result would constrain how CBCT thickness is used as a clinical criterion and as a research endpoint.

Conclusions. The protocol is feasible without added surgery or added radiation, but the reference standard can classify breach and wall-edge thickness only, not the thickness of intact covering bone. No data exist yet.

1. Introduction

Buccal bone thickness has become one of the most quoted quantities in implant dentistry. A wall of at least 1.5-2 mm is advised at placement, regenerative procedures are justified by reference to it, and cohort studies report change in buccal bone measured on CBCT as an outcome. All three uses share one assumption: that the imaging system measures what it is asked to measure. For thin bone next to a metal implant, that assumption is weakly supported. Several laboratory studies indicate that the thinnest walls disappear or are displaced on CBCT, so an intact plate of well under 1 mm may be recorded as absent, and a recorded ‘absence’ may therefore mean either a dehiscence or a plate too thin to resolve [1, 2, 3].

The consequence is practical. If CBCT calls thin intact bone a dehiscence, a clinician may add augmentation or open a site that did not need it. If CBCT calls a dehiscence intact, a defect is missed. In research, a systematic error that depends on true thickness distorts any analysis that regresses clinical outcome on CBCT-measured thickness, because the exposure is mismeasured most badly in the range where the clinical threshold is claimed to lie.

The evidence is also oddly shaped. Ex vivo and animal studies are numerous, and the best-known systematic review of CBCT for peri-implant bone loss found that its included studies were laboratory or animal investigations rather than clinical ones [4]. A human in vivo study with an intra-surgical reference would be simple in principle: patients undergoing flap surgery at an implant already expose the buccal bone, so direct inspection is available at no added risk. We could not find one (Section 3). This manuscript therefore proposes it.

We state three limits at the outset. First, the study cannot directly measure the thickness of intact bone that stays covered, because that would require removing bone; the reference standard classifies breach and measures the exposed wall edge. Second, no radiation exposure for research alone is proposed in the primary cohort; the radiation question is handled by design (Section 4.7). Third, nothing here has been performed; every number that is not attributed to a source is an assumption or the output of a calculation reported in Section 4.7 and in the accompanying script.

2. Background and critical appraisal of the evidence

Origin of the buccal wall rule

The 2 mm figure traces to a large dataset in which facial bone thickness at stage one was related to later marginal bone response, with more than 3,000 implants and a fall in bone loss as thickness approached 1.8-2 mm [5]. The observation was made with calipers after osteotomy, so thickness was measured by direct contact and not by imaging, and the mean observed thickness was only 1.7 mm (from the notes underlying this review). A beagle dog experiment of 12 animals and 72 implants later proposed 1.5 mm as the critical wall [6], and a recent consensus adopted below 1.5 mm as unfavourable [7]. The threshold has moved between 2, 1.5 and 1 mm across studies.

Contrary evidence exists. A 12-month study of 47 implants found that thin plates did not lose more bone except after open-flap one-stage surgery [8]. An older systematic review found insufficient evidence for a minimum thickness [9], and a 2023 systematic review noted inconsistent definitions of the critical thickness [10]. A randomized trial of small buccal dehiscences at posterior implants (22 patients) reported full survival and healthy tissues at 7.5 years with or without regeneration [11], although an earlier trial of untreated dehiscences reported more vertical bone loss over 6-18 months [12]. Achieving 2 mm after ridge preservation is also uncommon [13]. This manuscript does not adjudicate the rule. Its point is that every clinical test of the rule that relies on CBCT inherits the measurement error discussed next, and that the original caliper-based data cannot be reproduced from images unless the image error is known.

Evidence that CBCT fails for thin bone

Table 1 sets the pivotal studies against each other. In an ex vivo study with two scanners, blooming from the implant enlarged its apparent size by 12-15%, buccal bone thickness was underestimated by about 0.3 mm, and a further 0.45 mm ‘doubtful zone’ could not be classified [1]. An experimental study found the buccal bone not visible in 60-68% of cases, with the odds of detection rising steeply for each additional millimeter of true thickness [2]. A laboratory study on 36 porcine blocks reported that at a thickness of 1 mm or less specificity for the intact wall was 12.5%, meaning most intact thin walls were called defective, with a mean level error of 1.6 mm, and found that abutment and crown material did not matter [14]. An earlier study of cortical thickness adjacent to implants found the result scanner-dependent and poor below about 0.8 mm [15].

The one study that combined ex vivo and in vivo work used a visualization method that substitutes a pre-operative bone model and a standard implant model into the post-operative scan. Ex vivo, raw CBCT underestimated bone thickness, especially at the implant shoulder; in 52 implants in vivo, areas of 0-0.5 mm thickness were not visible and areas of 0.5-1.0 mm were occasionally visible [3]. This is the nearest approach to human evidence, but its in vivo comparison was between raw CBCT and a computed reconstruction, not between CBCT and surgically verified anatomy, and the reconstruction is itself an inference. The authors conclude that CBCT alone is insufficient to warrant surgical intervention [3].

The strongest dissent comes from a minipig study with histology as the reference, which reported an intraclass correlation of about 0.99 [16]. Its mean bone thickness was 5.1 mm, so thin bone was not tested, and it is better read as evidence that CBCT works in thick bone than as a contradiction. An animal study reported a mean difference of -0.22 mm with a standard deviation of 0.77 mm, a spread that is wide relative to a 1 mm clinical threshold, and it could not judge complete implant coverage [17]. Around natural teeth, a histologic comparison found CBCT overestimating buccal bone, with intraclass correlations of 0.53 or less [18]; the direction of error therefore differs between settings, which means that signed error cannot be assumed constant across implant, tooth and thickness.

Peri-implant defect detection and the artefact problem

A systematic review of CBCT for peri-implant bone loss included 18 studies (13 in vitro and 5 animal, none clinical) and judged performance good for circumferential and fenestration defects but moderate to low for dehiscence [4]. A later meta-analysis of 24 studies reported an area under the curve of 0.79 for titanium and 0.69 for zirconia, not significantly different, and 0.73 for dehiscence versus 0.87 for fenestration [19]. This is odd given that artefacts are physically greater around zirconia than titanium in vitro [20]. A plausible reading, which the present design can test, is that laboratory defects are drilled, large (about 3 mm in several studies, per the notes) and scored in clean phantoms, which hides the effect of artefact.

Metal-artifact reduction has repeatedly shown no significant benefit: for dehiscence and fenestration detection around zirconia implants [21], for titanium-zirconium and zirconia implants across tube voltages [22], and the adjacent zirconia implant lowered the area under the curve from 0.88 to 0.80 without statistical significance [23]. Further in vitro MAR evaluations exist [24, 25, 26]; we cite them at title level only. Machine-learning MAR has been reviewed [27], but without human validation. In a 2026 ex vivo study on sheep heads, fenestrations were detected with about 94% sensitivity and 95% specificity, whereas dehiscences reached about 70% sensitivity with 60-67% specificity, and neither voxel size (0.2 versus 0.4 mm) nor software changed this significantly [28]; the model concerned teeth, not implants, but it indicates that the dehiscence task is harder than the fenestration task even without metal and that voxel size is not obviously the controlling variable. Another 2026 experimental study examined implant material, position in the field of view and exomass [29].

Optimised ex vivo work gives an upper bound: at a single titanium implant, CBCT detected defects with 100% sensitivity and specificity and classified defect type with 86% and 99% [30]. High performance in one clean setting and failure in another are compatible; the spectrum of defects, the thickness distribution and the presence of adjacent metal differ. Only a clinical series can say where patients lie between them.

Table 1. Pivotal studies on CBCT visibility of thin peri-implant bone and defects (abstract-level appraisal).
StudyDesign and nMain findingMain bias or limitLevel
Vanderstuyft 2019 [1]Ex vivo, two scannersBlooming 12-15%; bone underestimated about 0.3 mm plus 0.45 mm doubtful zoneEx vivo; no soft tissue or motionB
González-Martín 2016 [2]ExperimentalBone not visible in 60-68%; detection odds rise per mmExperimental settingB
Domic 2021 [14]36 porcine blocksAt 1 mm or less, specificity 12.5%; level error 1.6 mmLaboratory; titanium onlyB
Lan 2022 [3]Ex vivo bovine plus 52 implants in vivo0-0.5 mm invisible; 0.5-1.0 mm occasionally visibleIn vivo reference was a computed modelC
Gröbe 2017 [16]Minipig histologyICC about 0.99Mean thickness 5.1 mm; thin bone untestedC
Pelekos 2018 [4]SR, 18 studies13 in vitro, 5 animal, none clinicalHeterogeneous laboratory designsB
Chagas 2021 [19]SR/MA, 24 studiesAUC Ti 0.79, Zr 0.69, n.s.Drilled defects, clean phantomsC
Freire 2024 [21]In vitro, zirconiaMAR no significant benefitPhantomC
Hartung 2026 [30]In vitro pilot, one Ti implantCBCT 100%/100% detectionOptimised setting; upper boundC

Note: Level is an operational category (A strong, B moderate, C preliminary, D mechanistic or theoretical, E speculative hypothesis), not a GRADE rating. n.s., not significant; SR, systematic review; MA, meta-analysis.

Competing modalities and registered work

Ultrasound and dental MRI avoid ionizing radiation. A cadaver study of 7 cadavers and 17 implants reported ultrasound agreement within 0.03-0.24 mm [31]. A 2025 systematic review of ultrasound in implant dentistry (17 clinical studies, 371 patients) reported concordance with CBCT with mean deviations below 0.5-1 mm and called for standardized large-scale clinical studies [32]. A 2026 in vitro study on 78 implants in bovine rib compared CBCT, ultrasound and intraoral scanning with direct measurement [33], and a 2026 critical review described ultrasonographic markers for peri-implant diagnosis [34]. For MRI, a review found mostly feasibility work [35], an in vivo study of 30 participants and 45 implants addressed MRI-based guide planning rather than buccal bone [36], and an in vitro pilot reported 98% sensitivity and 100% specificity for MRI at a single titanium implant [30]. Photon-counting CT reduced error ex vivo from 0.39 mm for conventional CBCT to 0.06 mm (from the notes) [37]. None of these has a patient-level intra-surgical reference for buccal bone. Our searches of ClinicalTrials.gov for CBCT peri-implant defect and CBCT buccal dehiscence returned interventional augmentation and ridge-preservation trials, and none that registered a diagnostic-accuracy design for this question; this is a search result, not proof of absence.

3. Hypothesis and theoretical framework

What the originality search found

We searched PubMed, Europe PMC (including preprints) and ClinicalTrials.gov under several vocabularies: re-entry, intra-surgical and intraoperative reference, caliper measurement, second-stage surgery, dehiscence and fenestration, defect configuration, cadaver and histology, and ultrasound and MRI comparators. Several targeted PubMed queries returned no records. The closest items are: the ex vivo and in vivo thickness study that used a model-substitution method rather than a surgical reference [3]; a 2026 comparison of CBCT, ultrasound and intraoral scanning against direct measurement in bovine rib, which is in vitro [33]; a 2022 laboratory study of low-dose CBCT in bovine bone with lesions, again in vitro [38]; and a dog study of bone-level assessments after reconstructive treatment of experimental peri-implantitis, which reported that periapical radiographs overestimated bone level by about 0.3-0.4 mm compared with CBCT and histology (from the notes) [39]. None used human surgical findings as the reference for CBCT. Embase, Scopus and Web of Science were not accessible, so a conference abstract or a non-English clinical report may exist that we could not see. The idea therefore survives, with the narrowing already described: the human reference is for breach status and wall-edge thickness, not for the thickness of intact covering bone.

Formal statement

Let a buccal site s on implant i in patient p have true state D_s∈{0,1} (1 = breach: implant surface exposed, that is, dehiscence or fenestration, on direct inspection after flap elevation and debridement). Let t_s denote the true thickness of the buccal wall in millimeters, defined at the wall edge for breached sites and by a proxy for intact sites (Section 4.4). Let Y_s be the CBCT call under a given configuration k (MAR on or off, voxel size, scanner), with Y_s=1 meaning breach.

Define accuracy conditional on thickness stratum: Se_k(t)=P(Y_s=1∣D_s=1,t_s=t) and Sp_k(t)=P(Y_s=0∣D_s=0,t_s=t). The hypothesis is that, for a thin-wall stratum T={t<1 mm}, Se_k(T) and Sp_k(T) are not both greater than 0.80 for any configuration k in the study, and that Se_k(T)−Se_(k′)(T) is not distinguishable from zero for MAR on versus off.

Physical mechanism

Two effects reduce the signal of a thin plate.

Partial volume and system blur. Model the reconstructed image of a bone plate of thickness t (mm) as the plate convolved with a Gaussian point-spread function of standard deviation σ=FWHM/2.355. For a slab much wider than σ, the peak fraction of full bone-to-soft-tissue contrast that survives at the plate center is

C(t)=erf​(t/(2√(2) σ))

where C is dimensionless (0 to 1), t and σ are in mm, and erf is the error function. The effective blur is at least the voxel edge v (mm) and in practice larger, since it includes focal spot, detector, scatter and reconstruction filter; we therefore treat FWHM as an assumed parameter, not as equal to v. A plate thinner than one voxel edge occupies a fraction t/v of the voxel, and the voxel value is a mixture of bone and soft tissue; for t/v<1 the mixture falls below bone density by construction.

Beam hardening adjacent to metal. Near titanium or zirconia, low-energy photons are preferentially removed, producing dark bands and streaks and, with blooming, an apparent enlargement of the implant [1]. We represent the net effect as a fractional loss δ of bone contrast in the zone next to the metal. A plate is classified present when the remaining contrast exceeds a decision threshold fraction θ of full contrast, that is, when C(t)(1−δ)≥θ. The minimum detectable thickness is then

t_(min)=2√(2) σ erf^(−1)​(θ/(1−δ)),  θ<1−δ

and no thickness is detectable if θ≥1−δ. Two consequences follow without further assumptions. First, t_(min) scales linearly with the blur, so halving voxel size helps only to the extent that it reduces total blur, which is dominated by non-voxel terms in many systems. Second, t_(min) grows without bound as δ→1−θ, so a modest additional contrast loss from metal can move a plate from detectable to invisible abruptly. MAR algorithms operate on projection or image data to reduce streaks; they do not restore contrast that was lost in a zone where the signal never reached the detector, which is one reason why MAR might not rescue the thin-wall case.

Illustrative computation under stated assumptions — not empirical data. We ran calc.py (saved in the paper folder) for FWHM of 0.3, 0.5 and 0.7 mm. Contrast recovery C(t) at t=0.5 mm was 0.95, 0.76 and 0.60 respectively, and at t=1.0 mm was 1.00, 0.98 and 0.91. With θ=0.5 and δ=0, t_(min) was 0.17, 0.29 and 0.40 mm. With θ=0.5 and δ=0.3 it was 0.27, 0.45 and 0.63 mm. With θ=0.6 and δ=0.3 it was 0.37, 0.62 and 0.87 mm, and with θ=0.6 and δ=0.4 no thickness was detectable at any FWHM. The parameters θ, δ and FWHM are assumptions chosen to span a plausible range; they are not measured values, and the model ignores noise, the cortical-versus-cancellous density difference, anisotropy and the shape of the interface. What the calculation does show is that detectability thresholds in the range 0.3-0.9 mm arise from ordinary parameter values, that the threshold is sensitive to δ, and that the observed ex vivo thresholds near 0.5-1 mm [2, 3, 14] are not surprising.

Figure 1 summarizes the mechanism. The model also predicts something the ex vivo literature has not isolated: the false-dehiscence error for thin intact plates should be as common as the missed-dehiscence error, because both arise from the same loss of contrast. That is consistent with the specificity of 12.5% at 1 mm or less reported in a laboratory study [14], and it is why specificity is a co-primary outcome here.

Explicit assumptions

A1. Direct inspection after flap elevation and debridement classifies breach correctly (reference standard error is small compared with CBCT error); we test this by duplicate blinded assessment of photographs and scans. A2. The anatomical state does not change between CBCT and surgery within the permitted interval. A3. Readers interpret CBCT in a standardized plane perpendicular to the implant long axis. A4. Sites within one patient are positively correlated (intracluster correlation assumed 0.30). A5. Breach prevalence among eligible sites is about 35% (assumption, no sourced estimate). A6. The thin-wall proxy for intact sites (Section 4.4) is monotone with true thickness.

Falsifiable predictions

P1. In the thin-wall stratum, at least one of Se_k(T) and Sp_k(T) is at or below 0.80 for the primary configuration. P2. Accuracy (area under the clustered ROC curve) is higher in the not-thin stratum than in the thin stratum. P3. The Bland-Altman bias for wall-edge thickness (CBCT minus caliper) is negative on average, and its absolute value grows as thickness falls. P4. MAR on versus off differs by less than 0.05 in area under the curve in the thin stratum. P5. Titanium and zirconia do not differ materially in thin-stratum accuracy, a prediction that mirrors the meta-analytic finding [19] and conflicts with the physical expectation [20]; we regard it as the least certain. P6. Accuracy at the native voxel size is not materially greater than at resampled larger voxels in the thin stratum, which follows from the dominance of non-voxel blur and from the sheep-head result [28].

Refutation. P1 is refuted if sensitivity and specificity in the thin stratum both exceed 0.80, with the lower bound of the one-sided 97.5% confidence interval above 0.80 under the clustered estimate (the falsification rule suggested in our candidate notes). P3 is refuted if the mean bias is within ±0.1 mm across thickness classes. P4 is refuted if MAR yields a clustered paired difference in area under the curve whose 95% interval excludes zero in favor of MAR by more than 0.05. If P1 is refuted, the ex vivo literature does not transfer to patients and the 1 mm figure should be abandoned as a limit of imaging.

4. Proposed methodology

Design and reporting

A prospective, multicenter, single-gate diagnostic-accuracy cohort with consecutive enrollment, reported according to STARD 2015 [40, 41]. The index test is CBCT as acquired for clinical reasons; the reference standard is direct intra-surgical assessment. The study would be registered before enrollment and the analysis plan time-stamped; no registration exists at present.

Population and eligibility

Adults (18 years or older) scheduled for a surgical procedure at an existing implant in which the buccal aspect will be exposed by a flap: surgical treatment of peri-implantitis, re-entry after contour augmentation, stage-two uncovering with flap, or implant removal. Inclusion requires that the treating clinician has already decided that a CBCT is indicated for clinical reasons, independent of the study. Exclusion: pregnancy; CBCT not indicated; surgery planned more than 14 days after the scan (the interval is an assumption); intervening treatment at the site; implants with metal crowns that preclude interpretable images are not excluded but are recorded and analyzed as a stratum. Eligibility is a limitation: patients in whom CBCT is considered indicated differ from all patients with implants (Section 7).

Index test

CBCT acquired with the clinic’s standard protocol, with scanner, field of view, kVp, mA, voxel size, rotation and exomass recorded; cross-device extrapolation is not assumed, since device diversity is large and findings for one machine do not automatically apply to another [42]. For each scan, two reconstructions are produced from the same raw data when the vendor allows: MAR off and MAR on. Voxel-size comparisons use the native reconstruction against a resampled coarser reconstruction; a finer-than-native voxel cannot be created. Because acquisition voxel size differs between centers and is chosen clinically, between-patient voxel-size contrasts are observational and confounded by scanner; we pre-specify them as exploratory.

Three readers (two oral radiologists, one periodontist or surgeon) would calibrate on a set of ex vivo scans, then independently read each site in a standardized multiplanar view perpendicular to the implant long axis, blind to the reference, the surgical plan and each other. Per site they record breach (forced choice), a five-point confidence score, and wall-edge thickness at 0 and 1 mm apical to the margin. A subset of 20% is re-read after four weeks. Cases the reader declares uninterpretable are retained as a reported category and, for the primary analysis, forced to the nearer binary call by the confidence score; a sensitivity analysis counts them as errors.

Reference standard and target conditions

Table 2 sets out target conditions. After flap elevation and removal of soft tissue and granulation tissue, an examiner who has not been shown the CBCT records: (i) breach status per site (implant surface visible, with thread exposure), (ii) vertical height and width of any breach with a calibrated periodontal probe, (iii) wall-edge thickness at the bone margin with a calibrated fine caliper, to 0.01 mm, and (iv) photographs with a scale. An intra-operative intraoral surface scan is acquired of the exposed site to preserve geometry. A second blinded examiner repeats the measurements on photographs and scan, to estimate reference reliability.

A thin-wall proxy for intact sites is needed, because the thickness of an intact covering plate is not measurable without bone removal. We propose a pre-specified binary indicator recorded by the surgeon before debridement is completed: whether the implant thread contour is visible or palpable through the bone plate (suggesting a plate in the sub-millimeter range). Its relation to true thickness is assumption A6, not an established fact. Where an implant is removed with a trephine, or bone is removed for another reason, the resected block may be measured with micro-CT or by section as an exploratory validation of the proxy; the number of such cases cannot be planned.

Blinding and timing are the principal safeguards against incorporation bias. The surgeon will inevitably have seen the clinical CBCT; the reference measurement is therefore taken by a calibrated examiner not given the CBCT, and the second examiner works from photographs and scan, offline, without CBCT. The index-to-reference interval is at most 14 days; all readers see only the scan, implant type and site label.

Table 2. Target conditions, index-test definitions and reference standard.
Target conditionCBCT index definitionReference standardPrimary or secondary
Buccal breach (dehiscence or fenestration) per siteReader forced-choice call with confidence scoreImplant surface visible after debridementPrimary (Se, Sp)
Breach in thin-wall stratumAs above, restricted to stratumThin-wall proxy plus breach statusCo-primary
Wall-edge thickness at breached or crater sitesReader-measured thickness at marginCaliper, 0.01 mmSecondary (Bland-Altman)
Breach depth (vertical extent)Reader-measuredCalibrated probeSecondary
Defect class (peri-implantitis only)Reader classificationSurgical classificationExploratory
Optional comparatorsUltrasound or MRI at the same sitesSameExploratory

Sample-size reasoning

The primary precision-based calculation follows the usual normal-approximation form for a proportion. For an expected sensitivity Se and desired half-width d of the 95% confidence interval, the number of reference-positive sites is

n_D=(z_1−α/2^2 Se (1−Se))/(d^2),

and for specificity n_D=z^2Sp(1−Sp)/d^2 reference-negative sites, with z_(1−α/2)=1.96. If π is the prevalence of breach among eligible sites, the total number of sites is N=max{n_D/π, n_D/(1−π)}. Clustering inflates this by the design effect DEFF=1+(m−1)ρ, where m is the mean number of evaluable sites per patient and ρ the intracluster correlation of the reader’s error. The number of patients is N⋅DEFF/m, inflated by 1/(1−ℓ) for loss ℓ.

The inputs are assumptions. We assume Se=0.70, Sp=0.75, d=0.10, π=0.35, m=3 (mesiobuccal, midbuccal, distobuccal), ρ=0.30 and ℓ=0.15. No sourced estimate of the prevalence of breach in eligible sites exists in our search, so π must be replaced by a pilot estimate (Section 8).

Python reproduction (script calc.py, output saved in calc_output.txt): n_D=80.67→81 breached sites; n_D=72.03→73 intact sites; total sites by sensitivity 231.4 and by specificity 112.3, so N=232; DEFF =1+2×0.30=1.6; clustered sites 372; patients 372/3=124; with 15% loss, 146 patients. Sensitivity of π: the sensitivity requirement of 81 breached sites corresponds to 405 sites at π=0.20 and 162 sites at π=0.50 before clustering (checked below), so the main uncertainty is prevalence, and we pre-specify interim re-estimation of π and m from the first 40 patients, blinded to accuracy, with the target number of breached sites kept fixed.

For the falsification test in the thin-wall stratum, we use a one-sided test of H_0:Se≥0.80 against H_1:Se=0.60, with α=0.025 and power 0.90:

n=((z_(1−α)√(p_0(1−p_0))+z_(1−β)√(p_1(1−p_1)))/(p_0−p_1))^2,  p_0=0.80, p_1=0.60.

This yields 49.83, hence 50 reference-positive thin-stratum sites, or 80 after DEFF 1.6. Specificity is symmetric under the same values. Because refutation requires both bounds to exceed 0.80, the co-primary pair is an intersection-union test and needs no multiplicity adjustment. The subgroup of zirconia implants may be too small for inference: with only 30 reference-positive sites, the 95% half-width for an expected sensitivity of 0.70 would be about 0.164, and with 50 sites about 0.127 (computed). The zirconia comparison is therefore stated as estimation, not as a powered test.

Table 3. Sample-size assumptions and computed requirements (illustrative computation under stated assumptions, not empirical data).
QuantityValueSource
Expected sensitivity, specificity0.70, 0.75Assumption
95% half-width0.10Design choice
Breach prevalence per site0.35Assumption; pilot required
Sites per patient m; ICC ρ3; 0.30Assumption
Breached sites needed; intact sites needed81; 73Computed
Total sites unadjusted; after DEFF 1.6232; 372Computed
Patients; with 15% loss124; 146Computed
Thin-stratum breached sites for falsification test50; 80 after DEFFComputed

Statistical analysis plan

Primary. Site-level two-by-two tables per reader and configuration. Sensitivity and specificity with confidence intervals that respect clustering of sites within patients, using generalized estimating equations with an exchangeable working correlation and a logit link, or cluster bootstrap resampling patients; with three readers, reader is a random or fixed effect and results are reported per reader and pooled. Area under the ROC curve from the five-point confidence score by a nonparametric method for clustered data [43]. Thin and not-thin strata are analyzed separately and as an interaction of stratum with accuracy.

Agreement for thickness. Bland-Altman analysis of CBCT minus caliper wall-edge thickness [44]: mean bias, limits of agreement, and regression of the difference on the mean to test thickness-dependent bias (P3). Because several sites come from one patient and several readers read each site, the limits are estimated from a variance-components model (patient, site, reader, residual) in line with the method-comparison treatment of repeated observations [44]. A clinically tolerable limit of agreement is stated in advance as ±0.5 mm, half of the 1 mm threshold in question; this is an assumption, since no sourced tolerance exists. For orientation, with an assumed difference standard deviation of 0.40 mm the limits are ±0.78 mm, and the approximate 95% half-width of each limit is 0.174 mm with 60 independent pairs, 0.134 mm with 100 and 0.110 mm with 150 (computed with SE=s√(1/n+1.96^2/(2(n−1)))); the effective number of independent pairs is the number of sites divided by DEFF. With this assumed spread the limits (±0.78 mm) would exceed the ±0.5 mm tolerance.

Subgroups (prespecified). (1) Titanium versus zirconia implant material; (2) MAR on versus off, as a paired within-site comparison; (3) voxel size, native versus resampled within scans (confirmatory) and between scanners (exploratory); (4) adjacent metal restorations or implants; (5) indication (peri-implantitis versus other); (6) reader; (7) thin versus not-thin stratum. Subgroup tests are interaction tests; only (7) and (2) are treated as inferential, the rest as estimation with intervals, to limit multiplicity. Handling of missing data: sites with no reference are excluded and counted; patients with no CBCT after enrollment are excluded and counted, in the STARD flow diagram. Verification bias is limited because every enrolled patient receives the reference standard, but partial verification occurs at the site level if a buccal aspect cannot be exposed; those sites are excluded and described.

Competing modalities. Optional ultrasound (non-ionizing) can be recorded at the same sites on the same day, with the same reference. This part is exploratory, because ultrasound evidence is promising yet reported mainly in cadavers, in vitro, or with CBCT as comparator [31, 32, 33].

Radiation protection, justification and ethics

The radiation question has to be answered before the diagnostic one. Dental CBCT devices vary widely in dose and image quality, and CBCT use in implant dentistry has been described as requiring justification and optimization before clinical use [42]. The European Basic Safety Standards Directive is understood to require that medical exposures be justified and optimized, including exposures arising in medical research [45]. We saw only search listings of the Directive, not its full text; article numbers, dose constraints and national transpositions must be verified before submission. We take the following approach, which can be checked by an ethics committee and a radiation-protection expert.

  • No exposure solely for research in the primary cohort. A patient enters the study only if the treating clinician has independently decided that CBCT is indicated; the research then uses images that would have existed. (ii) MAR and voxel-size variants come from reconstruction of the same raw data, not from additional acquisitions, so the comparison costs no dose. (iii) Because dose differs between protocols, the exposure parameters are recorded and reported so that readers can see which dose levels the accuracy estimates apply to; a low-dose protocol has been evaluated in vitro for peri-implant lesions [38], and whether such protocols preserve accuracy for thin bone is a question for a later nested comparison, not for this cohort. (iv) A second, research-only acquisition (for example, high-resolution versus standard) is not proposed; if a later amendment proposed it, it would need separate justification, dose estimate and approval, and we do not claim it would be justified. (v) Consent explains that surgery and imaging proceed as planned irrespective of participation. (vi) Ultrasound, if added, is non-ionizing, and MRI would require implant safety verification and is not part of the primary protocol.

There is a design cost. Restricting to patients who are imaged anyway makes the spectrum of the cohort depend on local practice and introduces selection that cannot be corrected. The alternative of imaging all surgical patients to remove this bias is not defensible on radiation grounds. Ethics approval, registration and funding are not in place; none is claimed.

Bias control and feasibility

Spectrum bias: report enrollment by indication, scanner and prevalence; compare with non-enrolled eligible patients where consent allows. Review bias: readers and reference assessors blinded in both directions; random reading order; adding scans of patients without implant surgery as negative controls is not proposed, because it would require unnecessary exposure. Incorporation bias: reference taken by examiners not shown CBCT. Verification: all patients receive reference. Observer variability: calibration, duplicate reads, intraclass and kappa statistics. Feasibility: enrollment of 146 patients is unlikely at a single center, so multicenter recruitment is assumed, with scanner heterogeneity analyzed as a stratum and as a random effect.

5. Competing explanations and how the design discriminates among them

Four rival explanations exist for any observed in vivo accuracy.

Physics versus reader. If accuracy is poor, is that because contrast is lost or because readers lack training and criteria? Three readers with calibration, intraclass agreement and the confidence score allow the reader component of variance to be estimated; if the variance component for reader exceeds that for thickness stratum, the reader explanation gains weight. Under the physical hypothesis, accuracy varies mainly with thickness and metal proximity and little across readers.

Spectrum. Laboratory defects are large and drilled, whereas clinical breaches vary in size and tissue state. Stratifying by breach height and width and by indication shows whether accuracy rises with defect size, which is what the spectrum explanation predicts [19]; the physical hypothesis predicts a thickness effect at fixed size.

Reference error. A poor apparent accuracy could be an artifact of a flawed reference. Duplicate blinded reference assessment on photographs and scans estimates this error; if reference disagreement is near the CBCT error, the study cannot discriminate, and that is reported.

Optimistic transfer from ex vivo work. The thick-bone result [16] and the optimized single-implant result [30] predict that clinical accuracy matches ex vivo accuracy when thickness and metal are favorable. The thickness-by-accuracy interaction separates the two accounts: transfer predicts high accuracy in the not-thin stratum and low accuracy in the thin stratum, which is the hypothesis; a general failure in vivo would be visible in both strata and would point to a different cause such as motion, soft tissue or scatter. MAR and material contrasts address the artefact-specific explanations: if MAR on versus off makes no difference in the thin stratum, then the loss is not recoverable from the reconstruction side. The material contrast is the most informative single test of whether laboratory phantoms hide artefact, because physical artefact differs between titanium and zirconia [20] while meta-analytic accuracy did not [19].

6. Clinical and engineering implications

Conditional on the results, three paths follow. If thin-stratum accuracy is poor, CBCT alone should not be taken as grounds for surgical intervention at a site where the buccal wall is judged thin, consistent with the view of the one in vivo thickness study [3]; research endpoints should treat CBCT-measured thickness below about 1 mm as unreliable, and analyses of the 1.5-2 mm rule that rely on it should state the measurement error. If accuracy is high in vivo, the ex vivo literature is too pessimistic and the rule can be tested with CBCT as intended. If accuracy is intermediate, a calibration curve (probability of breach given reader score and thickness) could be published and used as a correction in thickness analyses, with the usual caution that corrections validated at one device do not transfer to another [42].

For engineering, the data would show whether MAR and finer voxels give gains where they matter, namely thin plates next to metal, and would define a benchmark for photon-counting CT, ultrasound and MRI against the same reference [30, 31, 33, 37].

7. Limitations

  • The reference standard cannot measure the thickness of intact covering bone; the thin-wall proxy is a surgical sign of unknown validity (A6). The thin-stratum conclusion is therefore conditional on that proxy, and the optional resected-block validation is opportunistic. 2. Wall-edge thickness is accessible only where bone margins are exposed, which selects breached and crater-type sites and may not resemble intact thin plates. 3. Enrollment is restricted to patients in whom CBCT is clinically indicated, a selected spectrum; there is no way to correct for this within the design. 4. The surgeon has usually seen the CBCT, so incorporation bias is controlled by procedure, not eliminated. 5. The 14-day interval and 35% prevalence, the ICC, accuracy expectations and 0.5 mm tolerance are assumptions. 6. The physical model is a one-dimensional caricature with assumed blur and contrast-loss parameters and cannot predict thresholds for a given scanner. 7. Zirconia implants may be too few for a powered comparison. 9. Evidence was appraised at abstract level; Embase, Scopus and Web of Science were not available; a comparable human study could have been missed. 10. Soft tissue, motion and patient-specific scatter are not modeled. 11. The study does not test whether correct detection improves any patient outcome; accuracy is a precondition for benefit, not evidence of it.

8. Conclusions

The clinical use of buccal bone thickness thresholds and of CBCT follow-up of peri-implant bone depends on an imaging capability that has been validated in the laboratory and in animals but not against surgical findings in people. A diagnostic-accuracy cohort nested in surgery that is already planned, using images that are already clinically justified, can fill that gap without added surgery and without research-only radiation. The design predicts that accuracy for breach status falls in the thin-wall stratum, that MAR does not alter this and that thickness bias is negative and grows as bone thins; each prediction can fail. The principal weakness is that the reference standard classifies breach and wall-edge thickness but cannot measure intact covering bone, so the thin-wall conclusion rests on a surgical proxy. Under the stated assumptions, about 124 patients (146 with allowance for loss) would give interval half-widths near 0.10 for sensitivity and specificity overall, but the figure depends on an assumed prevalence that should be replaced by pilot data.

Cite this paper

Jain S, Gupta A. Seeing Thin Bone: A Diagnostic Accuracy Protocol for Cone-Beam CT Assessment of Buccal Bone and Peri-Implant Defects Against an Intra-Surgical Reference Standard. Working paper. Center for Implant Dentistry; 2026. Available from: https://bayareaimplantdentistry.com/clinician-research-and-publications/cbct-thin-bone-diagnostic-accuracy-protocol

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