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How Accurate Is Accurate Enough? An Outcome-Anchored Threshold for Implant Positional Deviation and the Measurement Error of the Accuracy Endpoint

Paper type
Methodological Study (theoretical)
Status
Original Work · Working Paper
Keywords:
computer-assisted implant surgery · implant accuracy · positional deviation · measurement error · limits of agreement · minimal detectable difference · buccal bone
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. Static-guided, dynamically navigated and robot-assisted implant surgery are compared mainly on deviation from the planned implant position. Randomized trials and reviews report accuracy gains without demonstrated gains in survival, bone level or patient-reported outcomes. The label “clinically acceptable” and the 2 mm safety margin derive from pooled mean error, not from an outcome-derived threshold, and the deviation endpoint itself is measured with error.

Objective and hypothesis. We propose (H1) that adverse-outcome risk is governed by loss of margin in a consequence space (for example remaining buccal bone thickness) rather than by raw deviation, with a plan-relative change point; and (H2) that endpoint measurement error is comparable to inter-technology differences for classifying individual implants but small relative to them for comparing group means, unless the error is differential.

Proposed approach. A framework with three parts: geometric error propagation from platform offset, angle and implant length to apical and consequence-space deviation; a probabilistic link from a bivariate-normal deviation distribution to the probability of falling below a stated bone thickness; and a smallest-detectable-difference analysis based on published scan-versus-CBCT limits of agreement. Illustrative Python computations under stated assumptions show, for example, that lowering platform and apical spread from 0.8 and 1.0 mm to 0.5 and 0.7 mm changes the probability of residual buccal bone below 1 mm by 0.115 at a planned wall of 2.0 mm but by 0.024 at 3.0 mm. We specify a four-stage empirical design (endpoint test-retest, harmonized individual-participant data, error-corrected change-point modelling, prospective confirmation), a sample-size calculation, and eight numbered predictions with refuting results.

Expected contribution. A testable definition of an outcome-anchored threshold, a quantified account of when the accuracy endpoint is and is not adequate, and a reporting standard for deviation studies.

Conclusions. The framework is theoretical. Existing outcome-linked cut-points are exploratory and small; no validated, error-corrected, consequence-based threshold was found in the searched sources. Empirical derivation requires data not yet assembled.

1. Introduction

Computer-assisted implant surgery (CAIS) is evaluated, in most comparative trials, by how closely the achieved implant matches the virtual plan. A widely cited meta-analysis of static guides pooled twenty clinical studies and reported mean errors of about 1.2 mm at the entry point, 1.4 mm at the apex and 3.5 degrees in angle, and it advised a safety margin of 2 mm around vital structures [1]. The ITI consensus on digital technologies built on this evidence base [2]. Subsequent work compares static, dynamic navigated and robotic systems on the same metrics.

Two observations make this practice difficult to interpret. First, higher accuracy has not been shown to produce better clinical results. An umbrella review of thirteen systematic reviews found better accuracy with guidance but comparable survival and bone loss [3]. A meta-analysis of nine randomized trials found no overall difference in bone loss or survival between computer-assisted and freehand placement, with six trials at high risk of bias [4]. A meta-analysis of randomized trials of robotic surgery concluded that the accuracy advantage had not been shown to translate into clinical or patient-reported benefit [5]. Second, the accuracy endpoint is itself a measurement with an error. A paired in vitro method comparison reported scan-versus-CBCT 95% limits of agreement of roughly 0.6 mm at the implant base and 0.7 mm at the apex, and about 2 degrees in angle [6]. These widths are of the same order as the differences claimed between technologies.

The two observations are linked. If no threshold for harmful deviation is known, an accuracy difference cannot be called clinically important or unimportant. If the measurement is noisy, observed differences and any dose-response relationship are distorted. An expert review titled “beyond accuracy” has already argued for outcome-based evaluation of CAIS [7]; the present manuscript asks the more specific question of what an outcome-based threshold would be, how it should be defined, and how measurement error limits its derivation.

This is a methodological and theoretical paper. It contains no new patient data. Its contributions are (a) a definition of an outcome-anchored threshold expressed in consequence space; (b) a quantitative framework for geometric and measurement error, with illustrative computations that were actually run; (c) a design to derive the threshold empirically; and (d) falsifiable predictions.

2. Background and critical appraisal of the evidence

Origin of the accuracy paradigm and the 2 mm margin

The accuracy literature on guided surgery was systematized in systematic reviews of computer technology in implant dentistry [8], and updated in the 2018 meta-analysis of static guides [1]. The question those reviews answered was geometric: how far does the achieved implant lie from the plan? The safety margin followed from the pooled error distribution, in the sense that margins larger than the typical error were considered prudent. This is an engineering tolerance, derived from the performance of a process, not from the consequences of deviation for patients. That distinction is the starting point of this paper. A tolerance set from process capability can be entirely reasonable as a safety rule (for example, keeping a distance from the inferior alveolar canal) and still say nothing about the deviation at which esthetic or biologic complications become more likely.

Pooled estimates for newer systems keep the same framing. Syntheses have compared static, dynamic and robotic approaches in general [9, 10] and in immediate placement [11]. A meta-analysis of robotic surgery pooled 27 studies and 1,546 implants and reported a mean platform deviation of 0.67 mm, apex 0.71 mm and angle 1.68 degrees [12]. None of the abstracts we read relates the pooled deviation to a clinical consequence.

What is known about position and outcome

Buccal bone is the best-developed link between position and consequence. A position paper on immediate placement lists a horizontal gap of at least 2 mm between the implant shoulder and the buccal wall among the prerequisites for a predictable outcome and prefers guided surgery to achieve it [13]. A systematic review of 12 clinical and four preclinical studies concluded that thin buccal walls are more prone to dimensional change, vertical bone loss and recession, and noted inconsistency in how a critical thickness is defined [14]. A network meta-analysis of immediate placement related approaches to buccal bone thickness and mid-facial recession [15], and a 10-year prospective study followed single immediate implants [16]. These sources link a thin wall to adverse outcomes. They do not link achieved deviation to the thickness that results, because the planned thickness and the deviation are rarely analyzed together.

Studies that relate achieved deviation to outcomes are few and small. A retrospective study of 180 implants in 90 subjects found no association between radiographic malposition (defined by earlier criteria) and peri-implantitis, whereas an emergence profile angle of 45 degrees or more (odds ratio 9.1) and a history of periodontitis were associated [17]; an erratum exists for that paper. A cross-sectional study of 452 implants in 100 patients associated several local factors with peri-implantitis [18]. In 27 patients with single-tooth guided implants in the anterior maxilla, mean shoulder deviation was 0.84 mm, and deviations of 0.8 mm or more were associated with a lower Pink Esthetic Score after a mean follow-up of 2.3 years [19]. This is, to our knowledge in the searched sources, the nearest published outcome-linked cut-point. It is a single-center study with a data-derived split, measured by CBCT superimposition, with no correction for measurement error and no external validation. A five-patient pilot with five-year follow-up reported correlations between buccopalatal linear inaccuracy and bone loss, probing depth, bleeding and keratinized mucosa that ran in the direction of more inaccuracy with better tissue values [20]; with five patients the finding cannot be interpreted. A systematic review of guided surgery in edentulous patients compares predicted with actual implant position, which is the geometric sense of accuracy only [21].

Taken together, the evidence is compatible with three readings: deviation within the usual range does not matter much for disease [17]; deviation matters for esthetics in the anterior maxilla [19]; or the existing studies are too small and too error-prone to tell. The design proposed here is intended to discriminate among them.

Accuracy gains in trials without outcome gains

The three-arm trial that compared robots, navigation and static guides (n=45) found comparable patient-reported outcomes, with the static guide fastest and associated with better recovery on day 3, and reported robot platform error equal to that of static guides [22]. A randomized trial of 36 patients found 0.70 mm versus 1.02 mm deviation favoring the robot, at the cost of 49.5 versus 24.4 minutes of operating time and more intraoperative discomfort [23]. A trial comparing a robot with navigation found 1.01 versus 1.78 degrees, no difference in linear deviation, and similar pain, edema and early success [24]. A multicenter trial of 140 patients reported 0.76 mm for a semi-active robot versus 1.48 mm freehand [25]. Long-term data are scarce: a five-year randomized trial of 20 patients reported no significant difference in implant failures between guided and freehand placement [26]. A review of patient-reported outcomes of static guided surgery found the evidence too thin for meta-analysis [27], a meta-analysis of flapless fully guided surgery found no randomized trial of flapless dynamic CAIS [28], and a recent review lists the outcomes still missing for robot-assisted dentistry [29]. Subgroup signals exist in both directions in the pooled analysis [4], so a null on the pooled outcome does not prove the absence of any effect in specific indications such as fresh sockets or the esthetic zone.

A terminology point matters for the proposal. A recent review separates outcomes (what is measured for patient meaningfulness) from outcome assessments, and cautions against conflating measurement tools with endpoints [30]. Deviation from plan is a technical performance measure; it becomes an endpoint of patient relevance only if it is shown to predict the outcomes that matter. That is a validation question, and it is the one examined here.

A cautionary parallel in arthroplasty

Orthopaedics offers a closely related history. A “safe zone” for acetabular cup inclination and anteversion was long used as an accuracy target in hip arthroplasty. A systematic review of 28 articles found that most could not identify a significant difference in mean cup angles between dislocating and non-dislocating hips and concluded that the safe zone could not be justified [31]. The zone was publicly declared dead in an editorial [32], and a functional safe zone that accounts for patient-specific pelvic motion was argued to be superior [33]. A case-control study of 56 dislocated hips explored whether a safer target could be defined [34], and a review documented that references to the original safe zone are frequently misquoted [35]. The lesson is methodological: a geometric target adopted for convenience and repeated in the literature can persist without outcome validation, and a better target may need to include patient-specific context. The parallel does not prove that implant dentistry will follow the same course. The anatomy, loading and failure mechanisms differ, and the effect of a safe zone in hips is a dislocation rate, an event far more frequent in some series than implant loss.

The measurement of the endpoint

Accuracy is usually measured by superimposing a postoperative CBCT on the planning CBCT, or by registering a postoperative intraoral scan to the planning data using the scan body. In a prospective clinical comparison, the two methods agreed on average (mean 3D difference 0.03 mm, SD 0.17 mm) [36]. A prospective cohort reported a root-mean-square difference of 0.29 mm between scan-registration and CBCT positions [37]. Implant blooming on CBCT, 12 to 15 percent of implant diameter in an ex vivo study of buccal bone thickness, shows that CBCT imaging distorts the implant boundary [38]. An in vitro validation reported no significant mean difference between the two assessment methods [39]. The most informative source is the paired in vitro Bland-Altman study: mean absolute scan-CBCT differences were 0.73 degrees, 0.22 mm at the base and 0.26 mm at the apex, with small bias and 95% limits of agreement of about -2.01 to +1.31 degrees, -0.62 to +0.53 mm and -0.73 to +0.58 mm; CBCT had a larger within-implant standard deviation than scans (0.55 versus 0.20 degrees), and agreement was worse in distal-extension sites [6]. Three limits apply. It was in vitro, in the posterior mandible only. It compared two methods against each other, so neither is a reference standard. It cannot reveal test-retest error on patients. We found no clinical repeatability study.

Table 1. Pivotal sources for the argument, with operational evidence levels.
Source (design, n)Finding relevant hereMain limitationLevel
Tahmaseb 2018 [1] (SR/MA, 20 studies)Pooled static-guide error; 2 mm margin advisedMargin from process error, not outcomesC
Tomar 2026 [3]; Shirani 2026 [4]; Ainoosah 2026 [5]Accuracy gain, no demonstrated outcome gainShort follow-up; high risk of bias in six trials [4]B
Monje 2023 [14] (SR, 12 clinical studies)Thin buccal wall linked to recession, bone loss; critical thickness inconsistentBaseline thickness, not deviationB
Fürhauser 2015 [19] (n=27)Shoulder deviation of 0.8 mm or more associated with lower PESSingle center, data-derived cut, no error correctionC
Corbella 2023 [17] (180 implants)Malposition not associated with peri-implantitisRadiographic definition; erratumC
Hoene 2026 [6] (180 paired measurements)Scan-CBCT limits of agreement; CBCT less reproducibleIn vitro; posterior mandible onlyC
Seagrave 2017 [31] (SR, 28 articles)Hip safe zone not supported by outcomesDifferent field; analogy onlyB

Note. Evidence levels are operational categories used in this manuscript (A strong, B moderate, C preliminary, D mechanistic or theoretical, E speculative), not GRADE ratings. Appraisal was at abstract level.

3. Hypothesis and theoretical framework

Formal statements

H1 (consequence-space hypothesis). For a prespecified adverse outcome Y (for example mid-facial recession of 1 mm or more at 3 years), the risk of Y depends on the margin remaining between the achieved implant and a consequence boundary (for example the buccal bone surface), and this dependence has a change point. Raw three-dimensional deviation predicts Y only through its component along the consequence direction and through the planned margin. An outcome-anchored threshold is therefore plan-relative: the same deviation is tolerable with a thick planned wall and harmful with a thin one.

H2 (endpoint-error hypothesis). The deviation endpoint has a measurement error whose spread is comparable to claimed inter-technology differences when classifying individual implants, but much smaller than those differences relative to the between-implant spread when comparing group means. The endpoint is adequate for group comparison and inadequate for threshold classification and dose-response estimation unless the error is estimated and corrected, and it can mislead in any setting if the error differs between arms.

Figure 1 summarizes the model. It is a conceptual illustration, not data.

Assumptions

(A1) Deviation components are approximately normal and unbiased unless a mean shift is stated. (A2) The platform offset and the apical offset in the consequence direction are positively correlated through the angular deviation. (A3) The outcome-relevant boundary is a plane (the buccal bone surface) at a known planned distance. (A4) Measurement error is additive, independent of true deviation, and has variance estimated from method-comparison data. (A5) Bone remodeling after placement is ignored; the computation concerns the initial margin, not the final bone level. These assumptions are simplifications. Registration error is spatially structured, and deviation distributions are right-skewed when magnitudes are used; the normal model is a tractable approximation for signed components.

Geometric error propagation

Let d_p be the lateral offset (mm) of the implant platform center from the planned platform center, α the angular deviation (degrees) of the implant axis, and L the implant length (mm). The lateral offset at the apex is the vector sum of the platform offset and the lateral displacement produced by the tilt. In the worst case, when both are coplanar and directed the same way,

d_(apex)≈d_p+Ltanα

and in general (d_p−Ltanα)≤d_(apex)≤d_p+Ltanα. If the platform offset and the tilt component are independent and each has per-axis standard deviation σ_p (mm) and σ_α (radians), then

σ_(apex)≈√(σ_p^2+L^2σ_α^2).

The Python script calc32.py (saved in the paper folder) gave, for d_p=1.0 mm, worst-case apical offsets for L = 8, 10 and 13 mm. At 3.5 degrees (the pooled static-guide angle in [1]) the offsets are 1.49, 1.61 and 1.80 mm; at 5 degrees they are 1.70, 1.87 and 2.14 mm. The angular term alone, at L=10 mm, adds 0.17, 0.35, 0.61 and 0.87 mm for 1, 2, 3.5 and 5 degrees. Hence one degree of angular difference between systems, the order of the robot-versus-navigation difference reported in [5] and [24], is worth about 0.17 mm at the apex of a 10 mm implant, below the 0.57 to 0.66 mm half-width of the scan-versus-CBCT limits of agreement [6]. With independent components, σ_p=0.5 mm and σ_α=2 degrees give σ_(apex)=0.61 mm, and σ_p=0.8 mm with 3 degrees gives 0.96 mm.

These numbers are geometry, not data. They show that for long implants the angle contributes as much as the platform offset, and that the pooled apical error exceeds the pooled platform error mainly because of this term.

From a deviation distribution to a consequence

Let x be the buccal component of the lateral offset (mm, positive toward the buccal plate). With a planned buccal wall thickness T_0 (mm) around the planned implant surface, the remaining thickness at the platform is T_p=T_0−x_p and at the apex T_a=T_0−x_a, and the minimum along the body is attained at one of the two ends because the axis is straight. We model (x_p,x_a) as bivariate normal with mean μ (mm), standard deviations σ_p and σ_a and correlation ρ. The probability that the remaining wall falls below a stated thickness t is

P(margin loss)=P(min(T_p,T_a)<t)=1−P(x_p<T_0−t, x_a<T_0−t).

For the platform alone this reduces to 1−Φ((T_0−t−μ)/σ_p); with T_0=2.5, t=1.0, μ=0 and σ_p=0.8 the closed form gives 0.0304 and a Monte Carlo run of two million draws gave 0.0305, which verifies the code. The two-dimensional case was computed by Monte Carlo.

Illustrative computation under stated assumptions, not empirical data. All distributions below are assumptions chosen for illustration. “Static-like” means σ_p=0.80 mm and σ_a=1.00 mm; “robot-like” means σ_p=0.50 mm and σ_a=0.70 mm; both use μ=0 and ρ=0.7 unless stated; t=1.0 mm. The labels do not claim to reproduce any published system. For orientation, an isotropic two-dimensional normal deviation with a per-axis spread of 0.8 mm has a mean radial offset of 1.0 mm, similar in order to the pooled static-guide entry error [1], while the probability that its buccal component alone exceeds 1.0 mm is 0.106.

Table 2. Illustrative probability that the remaining buccal wall falls below 1.0 mm at the platform or apex (Monte Carlo, 2,000,000 draws per cell; assumptions in text).
Planned wall T0 (mm)Static-likeRobot-likeAbsolute difference
1.50.3960.2890.106
2.00.2000.0850.115
2.50.0810.0170.064
3.00.0260.0020.024

Three points follow. First, the consequence of a given technology depends strongly on the plan: moving from a planned wall of 2.0 mm to 3.0 mm reduces the static-like probability from 0.200 to 0.026. Second, the absolute benefit of the more precise system is largest at moderate planned walls (0.115 at 2.0 mm) and small at 3.0 mm (0.024), although the relative reduction is large; a threshold stated only in relative terms would exaggerate the benefit in thick walls. Third, a systematic buccal shift is as important as spread. With the static-like spread, a mean shift of 0.3 mm toward the buccal plate at T_0=2.0 mm raises the probability from 0.200 to 0.310, more than the gap between the two technologies at that wall (0.115). This is consistent with the suggestion in the three-arm trial that the direction of error may matter as much as its size, since robots showed near-zero systematic error and guides or navigation a centrifugal pattern [22]. For a stricter boundary (t=0.5 mm, T_0=2.0 mm) the probabilities are 0.081 and 0.017.

The outcome-anchored threshold

We define the threshold on the consequence axis first and convert it to a deviation tolerance second. Let m be the remaining margin (for example buccal wall thickness at 1 year, measured on CBCT) and let r(m)=P(Y=1∣m,covariates) be the adjusted risk of the outcome. With a clinically chosen absolute risk increment Δ (for example 5 percentage points) over the risk at a reference margin m_(ref), the outcome-anchored margin is

m^*=sup{ m:r(m)−r(m_(ref))≥Δ }

and the plan-specific deviation tolerance is d_tol^*=T_0−m^* in the consequence direction. The choice of Δ is a value judgment and must be set by clinicians and patients before analysis, as in minimal-important-difference methodology; the data supply m^* with a confidence bound, not the value of Δ. A distinct safety margin (for example around the inferior alveolar canal) remains an engineering constraint and is not replaced by this construct. The 2 mm margin is therefore not wrong; it is a different kind of quantity.

Measurement error of the endpoint

Let the observed deviation be D_(obs)=D_(true)+b_k+e, where b_k is the bias of measurement method k and e∼N(0,σ_m^2). For a Bland-Altman comparison of two methods, the 95% limits of agreement are d±1.96 s_d, with s_d the standard deviation of the paired differences. If both methods have independent errors of equal variance, σ_m=s_d/√(2); if all discrepancy is attributed to one method, σ_m=s_d is an upper bound. From the published limits [6] we computed half-widths of 0.575 mm (base), 0.655 mm (apex) and 1.66 degrees, giving s_d of 0.293 mm, 0.334 mm and 0.847 degrees, and equal-error values of 0.207 mm, 0.236 mm and 0.599 degrees. The calculations below use the upper-bound values of about 0.29 to 0.33 mm to avoid understating the problem.

Four consequences follow.

Individual classification. An implant with true deviation exactly at a threshold of 1.5 mm is classified above it with probability 0.5; at true 1.2 mm with σ_m=0.29 mm the probability is 0.150, and at true 1.8 mm it is 0.850.

Group comparison. Random error adds variance σ_m^2 to the between-implant variance s_true^2. The minimal detectable difference between two arms at two-sided α=0.05 and 80% power is (z_(0.975)+z_(0.80))√((s_true^2+σ_m^2) 2/n) with n implants per arm (patient clustering ignored).

Table 3. Illustrative minimal detectable difference between two arms (mm), computed under the stated assumptions; σ_m uses the upper-bound value 0.29 mm.
True between-implant SD (mm)Per-arm nNo measurement errorWith σm=0.29 mm
0.5200.440.51
0.5450.300.34
0.51000.200.23
0.7200.620.67
0.7450.410.45
0.71000.280.30

Random endpoint error inflates the detectable difference by about 7 to 16 percent in these scenarios. The dominant limit is the small number of implants and the between-implant spread, not the measurement. With 45 implants per arm and a true spread of 0.5 mm, a 0.3 mm difference sits just below the detectable value of 0.34 mm even with perfect measurement; this concerns power, and all the trials cited above had samples of this order or smaller [22, 23].

Differential error. The comparison is not protected if the bias differs between arms (b_A≠b_B). Agreement worsened in distal-extension sites and at more distal positions [6], and CBCT distorts the implant boundary [38]. If arms differ in site mix, in the evaluation method (scan registration in one arm, CBCT in the other) or in the segmentation of the implant, a bias of 0.3 mm mimics a technology effect of 0.3 mm. We did not model this beyond stating the equivalence.

Regression dilution. In a dose-response analysis, random error in the exposure attenuates the slope by the reliability ratio λ=s_true^2/(s_true^2+σ_m^2). With s_(true) of 0.5 and 0.7 mm and σ_m of 0.29 mm, λ is 0.75 and 0.85; with 0.33 mm it is 0.70 and 0.82. A threshold estimated without correction is biased toward a larger tolerance (the data look flatter than they are).

The claim that limits of agreement are “as wide as the differences claimed” is therefore true for single implants: a robot-versus-navigation difference of 0.77 degrees [5] is less than half the 1.66 degree half-width, and an apical difference of 0.3 mm is about half the 0.66 mm half-width. It is not true for group means with adequate n when error is random and non-differential. This qualification is the main correction that this analysis makes to the initial framing of the problem.

Numbered predictions and refuting results

P1. After adjusting for planned thickness, remaining buccal wall at 1 year decreases with signed buccal deviation with a slope of about −1 (geometry). Refuted if the error-corrected 95% confidence interval for the slope excludes the range −1.3 to −0.5.

P2. The risk of the primary soft-tissue or bone outcome rises beyond a change point in the margin m. Refuted if a linear or flat model fits as well as a hinge model (AIC difference below 2) and no Δ-defined m^* exists within the observed range.

P3. Given the planned margin and the consequence-direction deviation, unsigned three-dimensional deviation adds no predictive information. Refuted if adding it improves AIC by more than 4.

P4. The lower confidence bound of the outcome-anchored tolerance d_tol^* exceeds the between-technology difference in at least one patient-relevant domain, so that current technology differences are clinically unimportant in that domain. Refuted if the bound is below 0.3 mm in all domains.

P5. Signed (directional) deviation is a better predictor than its absolute value, and d_tol^* is smaller in the anterior maxilla than in posterior sites. Refuted if absolute deviation predicts equally well or if tolerances do not differ by site.

P6. In patients, the scan-versus-CBCT limits of agreement are wider than the in vitro limits [6]. Refuted if the clinical half-widths are 0.5 mm or less and 1.5 degrees or less.

P7. At the threshold, more than 10% of implants within 0.3 mm of it are misclassified by the endpoint; arm-specific biases of 0.2 mm or more occur when evaluation methods differ. Refuted if misclassification is below 5% and arm-specific bias is below 0.1 mm.

P8. The error-corrected dose-response slope exceeds the naive slope by 15% or more. Refuted if the ratio is below 1.05.

If P1 holds but P2 fails, deviation acts through geometry yet does not alter outcomes within the achievable range, a result consistent with the null for malposition in [17].

4. Proposed methodology

The design is proposed and has not been performed. It has four stages (Figure 2); the first can be done on existing images and costs little, and the others depend on data sharing.

Stage 1: clinical test-retest and inter-software study of the endpoint

Design. Use postoperative CBCT and intraoral scans already acquired in one completed accuracy trial or consecutive case series. For each implant, two trained raters perform the superimposition twice, at least two weeks apart, in two planning-software packages, and a second scan is acquired at the same visit where the protocol allows. Estimands. Within-implant standard deviation S_w, repeatability coefficient 1.96√(2) S_w, inter-rater and inter-software bias and limits of agreement for platform offset, apical offset, angle, and the buccolingual, mesiodistal and depth components separately, by site type (bounded, distal-extension, fresh socket, edentulous arch). Sample size. For a method-comparison study, the precision of each limit of agreement depends on n and the SD of differences; sample-size methods for Bland-Altman analysis exist [40]. We used the approximation SE(LoA)≈s_d√(1/n+1.96^2/(2(n−1))). With s_d=0.30 mm, the 95% confidence half-width on each limit is 0.143 mm at n=50, 0.101 mm at n=100, 0.071 mm at n=200 and 0.058 mm at n=300 (computed). We propose at least 100 implants, 200 if stratifying by site type. Reference standard. None exists. A physical reference (implants with known position in a phantom with a coordinate-measuring machine) would separate bias from imprecision and should accompany the clinical study. Output. A minimal detectable change in mm and degrees by site type. This stage falsifies P6 and P7 and supplies σ_m for all later stages.

Stage 2: harmonized individual-participant data

Sources. Completed randomized trials and prospective cohorts of static, dynamic and robotic CAIS with post-operative 3D deviation per implant and follow-up of at least one year. Registered trials such as NCT07577245, NCT05892406 and NCT06059573 list positional accuracy as the primary outcome (noted in the candidate dossier; records not re-read), so available follow-up may be short, which limits the outcomes that can be analyzed. Registry note. A ClinicalTrials.gov query on dynamic navigation accuracy returned trials of dynamic against static or freehand placement; registration records were not systematically screened for outcome follow-up, and this screening is a task for the full project. Inclusion. Implants with planned position, achieved position (signed components), planned bone wall at the site if available, and at least one prespecified outcome. Harmonization. A common coordinate convention (buccolingual, mesiodistal, apicocoronal relative to the planned axis), a common outcome dictionary, and the evaluation method recorded as a covariate. Governance. Secondary use of trial data requires agreement of the original investigators and compatibility with the original consent; no data access is assumed.

Stage 3: dose-response and change-point modelling

Exposures. Signed buccal deviation at platform and apex; consequence-space margin m (planned wall minus deviation); unsigned 3D deviation as a comparison. Outcomes. Primary: mid-facial recession of 1 mm or more at the last follow-up of 1 to 3 years (soft tissue), or remaining buccal wall below a prespecified thickness at 1 year (hard tissue), depending on available data; secondary: marginal bone loss, Pink Esthetic Score, prosthetic complications, patient-reported outcomes, implant loss. The choice of primary outcome must be made before analysis. Models. Mixed-effects logistic and linear models with random effects for patient and trial; flexible exposure terms (natural splines) compared with a hinge (change-point) model by AIC and by bootstrap confidence intervals for the change point. Covariates. Planned bone wall and graft status, site, jaw, timing of placement, periodontitis history, prosthetic emergence profile angle (shown to be associated with peri-implantitis in one study [17]), and technology. Technology enters as a covariate to separate the effect of deviation from other technology effects such as flap-sparing. Measurement-error correction. Regression calibration or SIMEX using σ_m from Stage 1 by site type. Threshold. m^* and d_tol^* are defined as in Section 3.5, with Δ fixed in advance. Sample size. For a binary outcome with event proportion p and an odds ratio θ per standard deviation of a standardized exposure, an approximate requirement is n≈(z_(1−α/2)+z_(1−β))^2/{p(1−p)(lnθ)^2} for a small to moderate effect (an approximation; it assumes a normal exposure and no covariate adjustment). At α=0.05 and 80% power the computed numbers are 530 implants for p=0.10 and θ=1.5; 1,267 for p=0.10 and θ=1.3; 298 for p=0.20 and θ=1.5; and 713 for p=0.20 and θ=1.3. Attenuating the log odds ratio by λ=0.78 raises these to 872, 2,082, 490 and 1,171. Clustering of two implants per patient with an intraclass correlation of 0.3 gives a design effect of 1.3. A change-point model needs more data than a linear slope, so these are lower bounds. The existing accuracy trials have 20 to 140 patients [22, 23, 25], far fewer than needed for θ=1.3; pooling is not optional.

Stage 4: prospective confirmation

A prospective multicenter cohort, or a nested substudy in a future randomized trial, records planned wall, signed deviation with the Stage 1 repeatability protocol, and the primary outcome, and tests whether the threshold from Stage 3 predicts the outcome in new patients (calibration of risk above and below d_tol^*). A trial of non-inferiority of robotic against static guidance on a composite of buccal bone, esthetic score and complications at three years would test the technology question directly [3, 4]; its design is beyond the scope here.

Bias control, ethics and feasibility

Principal biases are confounding by plan and site (adjusted and stratified), selection through missing follow-up (inverse-probability weighting), operator learning (operator as random effect), non-comparability of outcome ascertainment across trials (outcome dictionary, blinded assessment where possible), and publication of exploratory cut-points. The deviation-to-outcome relationship from observational data is associational, not causal, because deviation is not randomized; Stage 4 reduces but does not remove this. The proposed work uses existing images and data; ethics approval and consent compatibility are to be established by the investigators and are not claimed here. Stage 1 is feasible in months; Stages 2 and 3 depend on access to trial datasets.

5. Competing explanations and how the design discriminates among them

No dose-response in the achievable range. If deviation stays within a range that rarely produces margin loss, outcomes will be flat. P2 and P4 discriminate: a flat risk curve and a change point beyond the data range would indicate that current technologies are all above the threshold of relevance in the tested indications. This is the reading favored by the null for malposition [17], and the design can confirm it.

Host and prosthetic factors dominate. Periodontitis history and emergence profile were associated with peri-implantitis in [17]; implant-level local factors in [18]. The multivariable models include these terms, and the change-point test is conditional on them. If the deviation term adds nothing after adjustment, the data would support this explanation.

Plan quality rather than execution. A perfectly executed poor plan scores well on deviation and still fails. Including planned margin and a plan-quality rating (for example planned wall, emergence angle) addresses this partly; deviation measures fidelity, not suitability, and this cannot be removed by adjustment alone.

Measurement error masking a real effect. Attenuation (P8) would produce flat curves. The error-corrected model, validated by Stage 1, distinguishes true flatness from dilution; if the corrected slope remains null, dilution is excluded as the cause up to the accuracy of the estimate of σ_m.

Differential evaluation bias. If trials of different technologies were evaluated by different methods, apparent technology differences could reflect the method (P7). Stage 1 quantifies arm-specific bias by method, and evaluation method is a covariate in Stage 3.

Technology effects not mediated by deviation. Flapless surgery, operating time, discomfort or learning curves may affect outcomes independently of deviation, as the trials of robot and static guides suggest for time and recovery [22, 23]. Including technology and deviation in the same model separates mediated from direct effects only under strong assumptions; mediation analysis is exploratory.

6. Clinical and engineering implications

If the predictions hold, three consequences could follow. For reporting, deviation studies would state the planned margin, the signed components in the consequence direction, the evaluation method and its repeatability, because without these an accuracy figure cannot be interpreted. For trial design, studies that adopt deviation as a primary endpoint would justify the smallest difference of interest by reference to an outcome-derived tolerance and would power themselves with the measurement error included; a trial powered for a 0.3 mm difference with 45 implants per arm and a spread of 0.5 mm is, on the calculation in Table 3, under-powered even with a perfect measurement. For clinical use, a plan-relative tolerance could be displayed in planning software, so that the tolerance shrinks automatically when the planned wall is thin, and so that positional errors would be reported against the consequence boundary rather than against the plan only. If P4 holds, differences of the size reported between current systems would be clinically unimportant in the domains tested, and cost, time and discomfort would then weigh more in technology choice. If P4 fails, the accuracy advantage would have clinical meaning in those domains, and trials designed for that outcome would be justified. All of these statements are conditional on empirical results that do not yet exist.

For engineering, the analysis suggests that reducing angular error in long implants and removing systematic directional shifts may be worth more, in consequence-space terms, than reducing random platform error already near 0.5 mm; this follows from the geometry in Section 3.3 and the mean-shift example in Section 3.4 and has not been tested with real systems.

7. Limitations

  • Abstract-level appraisal. All sources were appraised from PubMed abstracts retrieved on 17 November 2026. Effect sizes, definitions of malposition, and risk-of-bias details were not verified in full texts, and some statements about study content rest on abstract wording only.
  • Illustrative parameters. The computed probabilities depend on assumed spreads, a correlation of 0.7 and a normal model. The “static-like” and “robot-like” distributions are not fitted to data. Real deviations are skewed, spatially structured and operator-dependent. The numbers illustrate the form of the dependence, not its magnitude in practice.
  • One method-comparison source. The only formal limits of agreement we found were from one in vitro study of the posterior mandible [6]. Clinical error may be larger (soft-tissue movement, scan-body seating) or smaller. We used the upper-bound reading of σ_m deliberately, but this does not replace a clinical test-retest study. Neither method is a reference standard, so the limits of agreement describe disagreement, not error against truth.
  • Initial margin, not final bone. The probability model concerns the immediate margin after placement. Remodeling, grafting, immediate placement into sockets, and soft-tissue thickness modify the later outcome and are not modeled.
  • Outcome latency and heterogeneity. Recession and bone-loss outcomes require one to three years or more; the trials that report deviation mostly follow patients for months. Outcome definitions differ across studies, and a pooled analysis may be dominated by a small number of trials.
  • Causal interpretation. A dose-response in observational deviation data is associational. Surgeons may deviate deliberately in difficult sites, so deviation can be a marker of case difficulty.
  • Threshold is a value judgment. The increment Δ that defines “clinically relevant risk” cannot be derived from data; it requires patient and clinician input. Different outcomes will give different thresholds, and a single number may not exist.
  • Search limits. Embase, Scopus and Web of Science were not accessible. Search queries that were long often returned no hits in PubMed, so relevant studies using other vocabulary may have been missed. The claim that no validated outcome-anchored threshold exists applies to the sources searched.
  • Analogy. The hip safe-zone history is used only as a methodological caution; dental implants differ in anatomy, loading and outcome mechanisms.

8. Conclusions

The accuracy of computer-assisted implant surgery is reported against a plan, and its clinical importance has not been established by outcomes. In the searched sources we found small exploratory associations between deviation and esthetic or tissue outcomes, one null association between radiographic malposition and peri-implantitis, and no validated, error-corrected threshold expressed in a consequence space. We proposed such a definition, plan-relative and tied to margin loss, and computed under assumptions how the probability of margin loss depends on planned wall, spread and directional shift. We also corrected the starting claim about the measurement endpoint: the published limits of agreement are as wide as claimed technology differences for single implants but not for group means, unless error is differential, and they would bias dose-response estimates toward a larger tolerance. The framework generates eight falsifiable predictions and a staged design. It remains theoretical until the first stage, a clinical repeatability study of the endpoint, is performed.

Cite this paper

Jain S, Gupta A. How Accurate Is Accurate Enough? An Outcome-Anchored Threshold for Implant Positional Deviation and the Measurement Error of the Accuracy Endpoint. Working paper. Center for Implant Dentistry; 2026. Available from: https://bayareaimplantdentistry.com/clinician-research-and-publications/implant-deviation-outcome-threshold

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