Smaller Than the Ruler: Radiographic Marginal Bone Level Measurement Error Versus the Effect Sizes Claimed in Implant Trials — A Meta-Research Protocol
- Paper type
- Meta-Research Protocol (with a measurement-theory framework)
- Status
- Original Work · Working Paper
- Keywords:
- marginal bone level · measurement error · smallest detectable change · dental implants · meta-research · minimal important difference
Contents
Abstract
Background. Change in marginal bone level (MBL) on intraoral radiographs is among the most common primary outcomes in implant trials, and between-group differences of a few tenths of a millimeter are routinely interpreted in trials and meta-analyses. Reliability studies report examiner and method variation that, in some settings, is of the same order or larger. Two questions are often blurred: whether measurement error invalidates randomized group comparisons, and whether the differences and individual cut-offs in use are interpretable given that error.
Objective/Hypothesis. We hypothesize that (a) non-differential random measurement error reduces power and precision but does not bias randomized between-group mean differences; (b) most interpreted MBL effects are smaller than the individual-level smallest detectable change (SDC) under plausible error scenarios, are not anchored to any minimal important difference, and are rarely accompanied by a reported standard error of measurement (SEM); and (c) early bone-loss cut-offs of about 0.5 mm lie inside the SDC of non-calibrated settings.
Proposed approach. A pre-specified meta-research audit of a random sample of implant randomized trials with MBL as primary outcome. We define SEM, SDC, group-level SDC, attenuation, misclassification and sample-size inflation in closed form, tabulate them over a grid of SEM values (computed in Python for this manuscript, under stated assumptions), and specify eligibility, search, sampling frame, data items, primary and secondary audit outcomes, analysis, and a registration plan. Registration has not been done.
Expected contribution. A set of exact statements about what MBL measurement error does and does not invalidate; a benchmark that separates variance, individual-level and clinical-meaning questions; numbered, falsifiable predictions; and an audit design that avoids duplicating an existing reporting audit.
Conclusions. Measurement error is a problem of power, interpretation and individual thresholds, not of bias in properly randomized contrasts. Whether trials interpret effects smaller than the ruler is an empirical question that this protocol makes testable. No audit data exist yet.
1. Introduction
Marginal bone level is measured on a two-dimensional projection of a three-dimensional structure, usually by a human reader who locates a landmark on the implant and a landmark on the bone. Recent reviews place MBL at the center of implant outcome research: it reflects the integrity of supporting tissues, most change occurs early after installation and connection and typically stays within about 1 mm, further change after loading is commonly 0.1 to 0.3 mm in the first year, and reported measurement errors are in the order of 0.5 mm or less [1]. Roughly 15 to 25% of implants lose more than 1 mm [1]. A consensus report on core outcomes for implant dentistry trials names peri-implant bone level as a core outcome, but, as far as the abstract shows, it does not settle what size of change is measurable or important [2].
Three questions follow. First, how large is the measurement error of the radiographic method, expressed in millimeters? Second, how large are the differences that trials interpret? Third, what does error do to each type of inference: a randomized group comparison, a within-patient progression call, a prognostic cut-off? Conflating them produces two opposite errors: dismissing all MBL trials because the ruler is larger than the effect, and treating a high intraclass correlation coefficient (ICC) as proof that sub-millimeter differences are trustworthy.
This manuscript is a meta-research protocol with a measurement-theory framework. It does not report an audit: no trials were extracted, and every number in the computational section comes from formulas or a simulation with stated assumptions. The aims are to (i) state precisely what random and systematic measurement error do to each inference; (ii) specify a benchmark grid of SEM values with the corresponding SDC; (iii) specify an audit that compares claimed effects with that benchmark and with minimal important difference (MID) anchors; and (iv) give numbered predictions and the results that would refute them.
The originality of the question was checked before writing, because the reporting side is already covered. A 2025 meta-research of randomized trials published 2019 to 2023 examined how MBL was assessed on digital periapical radiographs [3]. Its abstract reports that, of 162 articles, 108 were excluded at full-text stage for methodological reasons, that 54 were analyzed, that calibration was unreported in 54%, that no statistic of examiner agreement was used in 59%, that blinding was unreported or unused in 50%, that MBL was the primary outcome in 61%, and that only two articles (3.7%) were at low risk of bias [3]. That audit did not, as far as its abstract shows, compare trial effect sizes with the error of the method. Section 2.6 and the novelty table describe the residual overlap and how this protocol is narrowed to avoid it.
2. Background and critical appraisal of the evidence
Evidence that radiographic MBL error can be large
Four lines of evidence, all read at abstract level, point to large error in some settings.
Walton and Layton asked more than 60 examiners from three professional groups to read radiographs of implants. When assessing 100 normal radiographs twice, a participant on average assessed 24% differently from themselves (median kappa 0.58) and 28% differently from other participants (median kappa 0.53), whereas agreement was far higher when a tolerance of one thread was allowed (median kappa about 0.93 to 0.96) [4]. The notes available for this paper add that the authors concluded that perceived changes below 1 mm probably reflect human variation. Agreement was expressed as thread position, not millimeters, so no SEM follows directly. The design is observational with a self-selected reader sample.
Serino and colleagues compared radiographic with intra-surgical bone loss at 46 implants in 24 patients with peri-implantitis, read by three examiners. Radiographs underestimated intra-surgical loss by 0.7 mm (mesial) and 0.6 mm (distal), only 21% of radiographic values matched the surgical value, over- or underestimation within 1 to 2 mm occurred in 57% of cases, and the variability between examiners was often within 1 to 2 mm [5].
Christiaens and colleagues reported, in a controlled clinical study, that intraoral radiography lacks accuracy for peri-implant bone level; the notes record clinicians’ mean underestimation of bone loss between 1.1 and 3.8 mm [6]. Cassetta and colleagues found that periapical films significantly misestimate bone level against surgical measurement [7].
In a second study from the same group of 268 implants in 142 patients, inter-observer agreement was 0.950 and intra-observer values were 0.980 and 0.973, yet the mean difference between radiographic and intraoperative measurements was 0.50 mm with a standard deviation of 1.55 mm (range 0 to 8 mm), and the authors concluded that periapical radiographs are reliable for bone level changes [8]. High agreement indices and a large per-site discrepancy from a reference can therefore coexist: the first is a reliability statement, the second a validity statement, and neither alone gives the SEM needed here.
Evidence that error can be small
Sakka and colleagues had three examiners measure 22 readings around 11 implants with a handheld magnifier and graticule and reported ICCs of 0.993 to 0.995 between examiners and 0.998 within an examiner [9]. The sample is tiny and the ICC depends on between-site spread. Strauch and colleagues examined 152 mini-implants on 50 randomly chosen panoramic radiographs from a clinical trial: initial ICCs exceeded 0.8, but 9% of sites were unreadable and 32% showed observer differences of 0.5 mm or more; after a consensus session and retraining, and after exclusion of further sites, all remaining differences were within 0.5 mm and the SDC at 95% credibility improved from 0.73 to 0.31 mm (intra-rater) and from 1.52 to 0.34 mm (inter-rater) [10]. That study explicitly related the SDC to a minimal clinically important change of 0.2 mm, and its abstract reports SDCs of 0.11 mm at a 50% credibility level [10]. Its setting (panoramic films, mini-implants, re-examination of discrepant sites, exclusion of unreadable films) limits transfer to periapical trials, and the exclusions are themselves a source of selection.
Error therefore depends strongly on acquisition and reading protocol, and reported values range from a few hundredths of a millimeter in tightly controlled reading to millimeters in unselected examiner samples.
Geometry and reference standards
Beyond reader variation, projection geometry contributes. In a bovine-bone test stand, measured defect extent departed more from the true extent as the angular deviation of the image receptor increased [11]. A typodont study evaluated the use of implant length as a calibration reference on paralleling-technique periapical films and proposed a customized position jig to improve accuracy [12]. Accuracy of radiographs has also been compared with cone-beam computed tomography and histology [13] and in experimental peri-implantitis after reconstructive surgery [14]. These studies are in vitro or preclinical, but they show that geometric error can be systematic, and systematic error that differs between arms is the kind that can bias a randomized comparison.
The origin of the measurement-theory concepts
The concepts needed here come from outside implant dentistry. Lachin summarized that the reliability coefficient is the proportion of total variation not due to measurement error, that it bounds the maximal correlation and slope in regression models, determines sensitivity and specificity when the measure is used for classification, and affects statistical power, and recommended that reliability be assessed by randomly selected duplicate assessments and reported like power [15]. Regression dilution from random measurement error is the general phenomenon in epidemiology [16]. Weir’s review set out the relation between the ICC and the SEM in test-retest studies [17]. In rheumatology, Bruynesteyn and colleagues showed that for paired radiographs of an individual, the SDC is the appropriate measure of reliably detectable progression, and that the traditionally calculated smallest detectable difference overestimates it; the point matters for the proportion of patients classed as progressing in trials [18]. In dentistry, Kropmans and colleagues applied the smallest detectable difference to temporomandibular outcomes and noted that most outcome studies compare group means, which says nothing about individual change or its clinical relevance [19]. Reporting guidelines for reliability studies [20] and quality criteria for measurement properties [21] exist; as far as the searches show, none has been applied to MBL trials as a benchmark for interpreted effects.
Where claimed effects sit
Effect magnitudes interpreted in the sources seen for this paper illustrate the scale problem. Retrospective cohort analyses of early bone loss have been used to propose cut-offs: in 508 implants, 96% of implants with more than 2 mm loss at 18 months had lost 0.44 mm or more by 6 months [22], and in 590 implants a threshold of 0.5 mm at 6 months was proposed [23]. A 2026 retrospective study of 261 implants reported survival of 67.8% versus 98.3% by early radiographic bone loss before loading, but its abstract carries a correction and defines exposure differently [24]. The notes record that both cut-offs come from one center without external validation. A narrative review describes the early and long-term crestal responses [25], a meta-analysis addressed MBL after 5 years in function [26], and across 102 trials in an industry-sponsorship meta-regression the notes record a mean MBL of 0.74 mm per year [27].
Between-group effects interpreted in meta-analyses are of smaller magnitude: 0.05 mm per HbA1c category [28], 0.05 mm in a review of bisphosphonates and denosumab [29], 0.75 mm in a review of history of periodontitis [30], and 0.83 mm in a study of proton pump inhibitor use [31]. These come from syntheses and observational designs and are cited only to show the range, not as examples of trial error. Crestal versus subcrestal placement shows the interpretive problem within randomized evidence: one meta-analysis of 10 randomized trials and 709 implants found no difference [32], another recommended subcrestal placement for bone-level implants and found large losses for subcrestal tissue-level implants [33], a third tallied 16 studies as 10 without difference, three favoring crestal and three favoring subcrestal [34], and a 5-year randomized trial of 55 implants in 11 patients reported -0.80 versus -0.99 mm, not significant [35]. Reading these results against a measurement benchmark requires the SEM, which none of the abstracts report.
What is already done and what is not
The reporting side is covered by the 2025 meta-research [3]. The conceptual side of relating the SDC to a clinically important change exists in one measurement study of mini-implants [10]. The narrative of what MBL means clinically exists in a 2026 review [1]. What was not found, within the limits of the search, is (i) an audit comparing interpreted trial effects with a benchmark of measurement error, (ii) a formal statement of which implant-trial inferences are and are not invalidated by that error, or (iii) an assessment of whether early bone-loss cut-offs lie within the SDC. This manuscript restricts its claims to those three gaps.
Summary of pivotal evidence
| Study | Design and sample | Main finding (abstract level) | Main limitation | Level |
|---|---|---|---|---|
| Walton and Layton 2018 [4] | Observational; more than 60 examiners; 100 radiographs read twice | About 24% self-disagreement, 28% disagreement with others; high agreement within one thread | Thread-based agreement, not mm; self-selected readers | C |
| Serino et al. 2017 [5] | Comparative; 46 implants, 24 patients with peri-implantitis; 3 examiners | Radiographs underestimated surgical loss by 0.6 to 0.7 mm; 57% within 1 to 2 mm error | Small, diseased sites, one clinical context | C |
| Christiaens et al. 2017 [6] | Controlled clinical study | Intraoral radiography lacks accuracy; clinicians’ mean underestimation 1.1 to 3.8 mm (notes) | Abstract only; reference standard not appraised | C |
| Cassetta et al. 2018 [8] | 268 implants, 142 patients; probe reference; 2 blinded examiners | ICC 0.95 to 0.98 but radiograph minus surgery 0.50 (SD 1.55) mm | Reliability and validity differ; probe is itself imperfect | C |
| Sakka et al. 2005 [9] | 11 implants, 22 readings, 3 examiners | ICC 0.993 to 0.998 | Tiny sample; ICC depends on spread | C |
| Strauch et al. 2024 [10] | 152 mini-implants on 50 panoramic radiographs; 3 raters | SDC 0.73 to 0.31 mm (intra), 1.52 to 0.34 mm (inter) after retraining; 9% unreadable | Panoramic, mini-implants, post hoc exclusions | C |
| Dos Reis et al. 2025 [3] | Meta-research; 54 RCTs analyzed (2019 to 2023) | Calibration unreported in 54%; no agreement statistic in 59%; 3.7% low risk of bias | Restricted to periapical RCTs after exclusions | B |
| Lachin 2004 [15] | Methodological review | Reliability governs correlation, slope, classification accuracy and power | Not specific to dentistry | D |
| Bruynesteyn et al. 2005 [18] | Methodological review (rheumatology) | SDC, not SDD, for paired films of individuals | Different imaging field | D |
| Galindo-Moreno et al. 2015 and 2022 [22, 23] | Retrospective cohorts, 508 and 590 implants | Early-loss cut-offs of 0.44 and 0.5 mm | One center; no external validation (notes) | C |
Note. Levels are operational categories used in this manuscript, not GRADE: A strong, B moderate, C preliminary, D mechanistic or theoretical, E speculative hypothesis.
3. Hypothesis and theoretical framework
Formal statement
Let a trial randomize implants or patients to arms 0 and 1, and let the estimand be the between-arm difference in mean MBL change, δ=E(Δ∣arm 1)−E(Δ∣arm 0), in millimeters. The central hypothesis has three parts.
H1 (what error does). Under non-differential random reading error, the estimator of δ is unbiased, its variance rises, power falls, and nominal Type I error is preserved when the standard error is estimated from the observed data.
H2 (what error does not rescue). Differential systematic error (for example, arm-related projection geometry or arm-related missing films) biases δ; high reliability does not detect it, because reliability is computed on repeated readings of the same film.
H3 (the audit hypothesis). In implant randomized trials with MBL as primary outcome, a majority of interpreted between-arm differences are smaller than the individual-level SDC under benchmark SEM scenarios of 0.2 mm or more, few trials report an SEM or SDC, and few anchor interpretation to a minimal important difference.
H3 is explicitly not an invalidity claim. A difference smaller than the individual SDC can be statistically and clinically real at group level, since averaging reduces error by the square root of the sample size. H3 states instead that the sentence “the difference is clinically relevant” requires an anchor that is generally missing, and that individual-level claims (progression, cut-offs, case definitions) are limited by the SDC.
Measurement model and definitions
For implant i at occasion j, the observed level is X_(ij)=T_(ij)+e_(ij), with true level T_(ij) (mm) and reading error e_(ij) of mean zero and variance σ_e^2. The observed change is D_i=X_(i2)−X_(i1)=Δ_i+(e_(i2)−e_(i1)), where Δ_i is the true change. If errors at the two occasions are independent, the error in D_i has variance 2σ_e^2. The ICC is the ratio of true to observed variance:
ICC=(σ_T^2)/(σ_T^2+σ_e^2)
The standard error of measurement and the individual smallest detectable change (95% level, both in mm) are:
SEM=SD√(1−ICC) SDC=1.96√(2) SEM≈2.77 SEM
where SD is the observed between-implant standard deviation of the measured quantity in the sample in which the ICC was estimated. Three consequences follow. First, the ICC is sample-dependent: the same SEM yields a high ICC in a sample with wide bone-level spread and a lower ICC in a homogeneous one, so a high ICC alone does not guarantee a small SEM. Second, the SDC applies to a change between two measurements of the same implant. Third, the factor √(2) assumes independent errors at both occasions. If both films are read by the same reader with the same holder, error may be positively correlated across occasions, which makes the true error in D_i smaller than 2σ_e^2; if re-acquisition error (re-positioning of the receptor and beam) is included, σ_e is larger than that obtained by re-reading one film twice. Reliability studies that re-read the same film capture reader error only. This is why the benchmark below is a scenario grid and not a single number.
The group-level counterpart for the mean change in a group of n implants is:
SDC_(group)=SDC/(√(n))
For a between-arm difference in mean change with n_0 and n_1 independent implants, the standard deviation of the error-only component is SEM√(2/n_0+2/n_1), and for n_0=n_1=n the error-only 95% limit is 1.96⋅2 SEM/√(n) (equal to √(2) SDC_(group)). This limit describes how much of the observed contrast could arise from reading error alone; it is not a validity threshold, because the observed standard error already contains that variance. When the outcome is a single reading and not a change, the factor 2 is replaced by 1 in the error variance. The share of observed variance attributable to reading error in a change-score outcome is f=2 SEM^2/SD_obs^2 with SD_(obs) the observed standard deviation of the change; for example, SEM=0.2 mm and SD_(obs)=0.5 mm give f=0.32. Trials in which implants are clustered within patients require the cluster-adjusted sample sizes in all formulas.
What error does to each inference
Table 2 and the paragraphs below were computed with the script mbl_error_calc.py in the paper folder, run on 17 November 2026. They are an illustrative computation under stated assumptions and are not empirical data.
| SEM | SDC (individual) | SDC/√n, n=20 | SDC/√n, n=50 | SDC/√n, n=100 | Arm-difference limit, n=50 per arm |
|---|---|---|---|---|---|
| 0.05 | 0.139 | 0.031 | 0.020 | 0.014 | 0.028 |
| 0.10 | 0.277 | 0.062 | 0.039 | 0.028 | 0.055 |
| 0.15 | 0.416 | 0.093 | 0.059 | 0.042 | 0.083 |
| 0.20 | 0.554 | 0.124 | 0.078 | 0.055 | 0.111 |
| 0.30 | 0.832 | 0.186 | 0.118 | 0.083 | 0.166 |
| 0.50 | 1.386 | 0.310 | 0.196 | 0.139 | 0.277 |
| 0.75 | 2.079 | 0.465 | 0.294 | 0.208 | 0.416 |
For reference, if the abstract-level SDC values of Strauch and colleagues [10] followed the same formula (an assumption, not verified), they would imply SEM values of about 0.26 and 0.55 mm for the first-round intra- and inter-rater data, and about 0.11 and 0.12 mm after retraining and exclusions. Using the ICC route with an assumed between-implant SD of 0.8 mm, an ICC of 0.90 corresponds to SEM 0.25 mm and SDC 0.70 mm, an ICC of 0.95 to SEM 0.18 mm and SDC 0.50 mm, and an ICC of 0.99 to SEM 0.08 mm and SDC 0.22 mm. Thus an ICC of 0.95, which would usually be labeled excellent, still implies an individual SDC of about half a millimeter under that assumption. The assumed SD of 0.8 mm is not taken from any source.
Random error and the randomized contrast. In a simulation of 20,000 two-arm trials with 40 implants per arm, a true difference of 0.20 mm and a true-change standard deviation of 0.5 mm (both assumed), the mean estimated difference was 0.199 mm with no reading error, 0.201 mm at SEM 0.2 mm and 0.201 mm at SEM 0.4 mm, while power fell from 0.433 to 0.352 and 0.226. This is consistent with H1: random error leaves the mean difference unbiased and removes power, in line with the general principle that reliability determines power [15].
Differential systematic error. Adding a constant offset of +0.10 mm to arm 1 readings (for example, from a systematic difference in receptor angulation between arms), at SEM 0.2 mm, shifted the mean estimated difference from 0.20 to 0.301 mm. Under a true difference of zero, the same offset gave a rejection rate of 0.130 against a nominal 0.05, with a mean estimated difference of 0.101 mm. This follows trivially from the model and is shown only to fix the boundary of H1.
Sample size. For a two-arm comparison of mean change with two-sided α=0.05 and power 0.80, the required number of implants per arm is:
n=(2 (z_(1−α/2)+z_(1−β))^2 (σ_T^2+2 SEM^2))/(δ^2)
with z_(1−α/2)+z_(1−β)=1.96+0.8416 and σ_T the true-change standard deviation (assumed 0.5 mm). Table 3 gives the results; the reliability of the change score, σ_T^2/(σ_T^2+2 SEM^2), is 0.926, 0.758, 0.581 and 0.333 for SEM of 0.1, 0.2, 0.3 and 0.5 mm.
| Target difference (mm) | SEM 0 | SEM 0.1 | SEM 0.2 | SEM 0.3 | SEM 0.5 |
|---|---|---|---|---|---|
| 0.1 | 393 | 424 | 519 | 676 | 1178 |
| 0.2 | 99 | 106 | 130 | 169 | 295 |
| 0.3 | 44 | 48 | 58 | 76 | 131 |
| 0.5 | 16 | 17 | 21 | 28 | 48 |
At a target difference of 0.2 mm, an SEM of 0.2 mm raises the requirement from 99 to 130 implants per arm (31%), and an SEM of 0.5 mm triples it; these figures scale with the assumed σ_T.
Attenuation. If a true correlation of 0.40 between a risk factor of reliability 0.9 and an MBL outcome is measured with outcome reliability 0.9, 0.7 or 0.5, the expected observed correlation is r_(obs)=r_(true)√(rel_x rel_y), equal to 0.360, 0.317 and 0.268 [15]. Random error in an outcome leaves a regression slope unbiased, whereas error in a covariate attenuates it, which matters for analyses relating early to late bone loss, since both are error-laden.
Misclassification at thresholds. Let the true change over six months be normal with mean 0.4 mm and SD 0.4 mm (assumed), observed change equal to true change plus error with variance 2 SEM^2, and let the cut-off be 0.5 mm. In a Monte Carlo of 10^6 implants (seed 20261117), 40.2% were truly at or above the cut-off. With SEM 0.1 mm the sensitivity and positive predictive value of the observed classification were 0.876 and 0.865 and 10.5% of implants were misclassified; at SEM 0.2 mm the corresponding values were 0.784, 0.750 and 19.2%; at 0.3 mm 0.721, 0.671 and 25.4%; at 0.5 mm 0.649, 0.577 and 33.2%. For a 1.0 mm cut-off, where 6.7% were truly above, the positive predictive value fell to 0.680, 0.426, 0.287 and 0.172 at the same four SEM values, because a low-prevalence class is dominated by false positives. The early-loss cut-offs of 0.44 and 0.5 mm [22, 23] are of the same size as the individual SDC at SEM 0.2 mm (0.55 mm), and a 1 mm criterion lies inside the SDC once SEM exceeds about 0.36 mm (a 2 mm criterion, about 0.72 mm). Whether such cut-offs discriminate later loss at cohort level is a different question from whether they are individually measurable.
Numbered predictions and refuting results
The following predictions apply to the audit described in Section 4 and to the framework above. Each is paired with the observation that would refute it.
P1. Among trials with an interpreted between-arm MBL difference, at least 80% will have a difference smaller than the individual SDC at the benchmark SEM of 0.30 mm (SDC 0.83 mm). Refuted if fewer than 60% fall below that SDC.
P2. Fewer than 10% of trials will report an SEM, an SDC, or limits of agreement in millimeters, and fewer than 25% will report any ICC with its confidence interval. Refuted if at least 25% report millimeter-scale error.
P3. Fewer than 10% of trials will cite an MID or any numerical anchor for the interpreted MBL difference. Refuted if at least 25% do.
P4. Among trials whose conclusions call a difference clinically relevant or superior, the proportion with a difference below the group-level error-only limit at SEM 0.20 mm will be below 15%, showing that most such claims are not noise-driven at group level and that the problem is interpretive, not statistical. Refuted if it exceeds 30%.
P5. Trials that report calibration with an agreement statistic will not differ in median effect size from those that do not (absolute standardized difference below 0.2). Refuted if the difference is at least 0.3, which would suggest reporting or design correlates.
P6. Individual-level cut-offs and progression definitions used in implant studies (0.44 mm, 0.5 mm, 1 mm, 2 mm) will fall within the individual SDC at benchmark SEM 0.30 mm in at least half of the cases. Refuted if fewer than a third fall within it.
P7. The proportion of trials with at least one item compatible with differential error (no blinding of the examiner, arm-specific missing films above 10%, no receptor holder) will exceed 40%, consistent with the reporting gaps already documented for blinding and standardization [3]. Refuted if below 20%.
4. Proposed methodology
Design and registration
The design is a cross-sectional meta-research audit of published implant randomized trials, with a pre-specified benchmark analysis (Figure 1 shows the conceptual model and Figure 2 the workflow). The protocol, the extraction form, the sampling seed and the analysis script would be registered and time-stamped on a public registry suitable for meta-research before any screening begins. Registration has NOT been done. No search for the audit itself has been run, no trial has been sampled, and no trial data have been extracted.
Eligibility
Included: randomized trials in humans (parallel-group or split-mouth) that evaluate dental implants or implant-related procedures and report MBL on two-dimensional intraoral radiographs (periapical or bitewing) as primary or co-primary outcome with a between-arm comparison, published from 2019 to 2025. The period overlaps the 2019 to 2023 window of the earlier meta-research [3] by design, to permit cross-checks, and extends it to 2025. Excluded: animal and in vitro studies; trials whose only MBL measurement is on panoramic radiographs or cone-beam computed tomography (analyzed as a separate secondary stratum if numbers permit); single-arm studies; conference abstracts; retracted trials (checked against PubMed retraction flags at the time of screening). Unlike the earlier audit, trials are not excluded for absent radiograph-type information or absent receptor holders; those facts are extracted as data, so that lack of standardization is analyzed and not used to remove trials from the frame.
Search and sampling frame
Planned sources are PubMed, Europe PMC, Cochrane CENTRAL and ClinicalTrials.gov. Embase, Scopus and Web of Science could not be accessed for this manuscript; the registered protocol should add them if the authors have access, and the limitation is stated in Section 7. The search combines implant terms, bone-level terms and randomized-trial terms, and is finalized with a librarian before registration. All records are screened in duplicate. Eligible trials form the sampling frame. If more than 150 eligible trials are found, a seeded random sample of 150 is drawn, stratified by publication year and by comparison domain (implant surface or design, connection or abutment, placement depth or timing, augmentation, loading protocol, systemic or drug factors). If 150 or fewer are found, all are analyzed.
The target of 150 is based on precision. The Wilson 95% interval for a proportion of 0.5 has limits 0.421 and 0.579 with 150 trials and 0.404 and 0.596 with 100; for a proportion of 0.8 it is 0.729 to 0.856 with 150 trials and 0.711 to 0.867 with 100 (script output).
Data items
For each trial, two reviewers extract independently:
- Bibliographic data, year, country, sponsorship, registration status, comparison domain, unit of analysis (patient or implant) and whether clustering was handled.
- Radiographic acquisition: technique (paralleling or bisecting), receptor holder, individualized or customized positioning device, geometric calibration reference (implant length, thread pitch, known dimension), digital or film, software, and the landmark definitions (implant shoulder or original crest).
- Reading procedure: number of examiners, blinding to allocation and time point, calibration before reading, handling of discrepancies, number and handling of unreadable or missing films by arm.
- Reported reliability: any ICC, kappa, SEM, SDC, minimal detectable change, limits of agreement or percent agreement, with the metric, its value, its confidence interval, and whether it was based on re-reading or on re-acquisition.
- Effect data: outcome definition (level or change), time points, per-arm means, standard deviations, sample sizes, between-arm difference δ with its confidence interval and P value, and the standardized effect.
- Interpretation: whether the abstract conclusion describes a difference as clinically relevant, superior or no different; whether a minimal important difference or clinically meaningful threshold is stated and what its source is; use of individual-level thresholds (success criteria, early-loss cut-offs, progression definitions) in the trial.
- Sample-size calculation: target difference, assumed SD, and whether measurement reliability is mentioned.
The extraction form follows the reporting domains in the earlier audit [3] and the guideline for reporting reliability and agreement studies [20] so that overlapping trials can be compared.
Benchmarks and anchors
Because trial-specific SEMs are expected to be rarely reported, the primary benchmark is a pre-specified scenario grid of SEM 0.10, 0.20, 0.30 and 0.50 mm, with 0.30 mm designated primary. The grid spans the range implied by the literature read for this paper: a narrative review reports measurement errors in the order of 0.5 mm or less [1], while the SDC values in a mini-implant study would imply SEM of roughly 0.11 to 0.55 mm if its formula matches the one used here [10], and examiner differences of 1 to 2 mm occur in unfavorable settings [5]. When a trial reports an SEM or the ingredients for it (ICC with SD, or limits of agreement), SEM_(trial) replaces the scenario value, and the SDC, group-level SDC and error-only limit are recalculated for that trial.
There is no accepted MID for MBL. The protocol therefore uses three exploratory anchors, none of which is claimed to be validated: (i) 0.2 mm, the minimal clinically important change that Strauch and colleagues related their SDC to [10]; (ii) half of the pooled standard deviation of change, a distribution-based convention; and (iii) the upper bound of the early physiological range of about 1 mm [1], to classify differences as within or beyond expected remodeling. Any MID stated by the trial itself takes precedence. An anchor-based MID would require patient-centered or prognostic outcomes linked to MBL, which is outside this audit.
Definition of an interpreted effect
An interpreted effect is the primary between-arm MBL difference in a trial when it is statistically significant at the trial’s own criterion or is described as favorable, superior or beneficial in the abstract conclusion.
Primary and secondary outcomes of the audit
Primary outcomes. - A1: the proportion of interpreted effects with (δ)<SDC at the primary scenario (SEM 0.30 mm; SDC 0.83 mm), reported with Wilson 95% intervals, and the same proportion at the other scenarios. - A2: the proportion of trials reporting at least one millimeter-scale error statistic (SEM, SDC, limits of agreement, or SD of duplicate differences). - A3: the proportion of trials stating a numerical MID or clinically meaningful threshold for the MBL outcome.
Secondary outcomes. - B1: for each trial, the ratio R=(δ)/L_(trial), where L_(trial) is the error-only 95% limit for the trial’s own sample sizes at each scenario SEM, and the proportion with R<1. - B2: the error variance share f=2 SEM^2/SD_obs^2 at each scenario, where SD_(obs) is the reported SD of change. - B3: the proportion of interpreted effects below each of the three anchors. - B4: the proportion of trials using individual-level thresholds, and of those the proportion whose threshold is smaller than the SDC at each scenario. - B5: the proportion of trials with features compatible with differential error: no examiner blinding, no receptor holder, arm-specific missing films exceeding 10%, or acquisition differing by arm. - B6: the association between reporting items (calibration, blinding, agreement statistic) and the standardized effect size. - B7: agreement of extraction with the earlier audit [3] for overlapping trials, and the proportion of sample-size calculations that mention reliability.
Statistical analysis plan
All outcomes are descriptive proportions with Wilson 95% intervals; no hypothesis test is used for P1 to P7 beyond comparing the interval limits with the refutation thresholds stated in Section 3.4. The association in B6 uses linear regression of the absolute standardized difference on reporting indicators with year and comparison domain as covariates, with robust standard errors; the association between claim strength and (δ)<SDC uses logistic regression with sponsorship, year and region as covariates. When SD_(obs) is not reported, it is derived from the confidence interval or P value using the standard conversions; if it cannot be derived, the trial is excluded from B1 and B2 and counted in a missing-data table. Sensitivity analyses vary the primary scenario SEM across the grid, repeat the analysis restricted to trials with a registered protocol, restricted to those with an examiner-blinding statement, and excluding trials where unit-of-analysis error (implants analyzed as independent despite clustering in patients) is suspected.
Bias control, ethics and feasibility
Dual independent screening and extraction follow a pilot on ten trials, with kappa of at least 0.8 required on categorical items; disagreements go to a third reviewer, and the analysis script is frozen at registration. The audit uses published data only; ethics review is expected to be unnecessary and is to be confirmed by the authors’ institution. The earlier audit analyzed 54 trials after stricter exclusions [3], so the frame here may fall below 150, in which case the census option applies. A separate optional study would estimate SEM directly by duplicate re-reading and re-acquisition in an ongoing trial, the only way to replace scenarios with measurements.
5. Competing explanations and how the design discriminates among them
Explanation 1: effects are small because the true biological differences are small, and the issue is clinical relevance, not measurement. This explanation predicts that effects are below any anchor (B3) but above the group-level error-only limit (B1), with a high share of trials in which the observed standard error is already small. It is compatible with H3 only in its interpretive part. The design reports (δ) against both the error limit and the anchors.
Explanation 2: calibrated trials have SEM below 0.1 mm, so the grid is too pessimistic. This predicts that trials reporting SEM or SDC have values below 0.15 mm and that A1 at SEM 0.10 mm is low. The design recalculates with SEM_(trial) where available and reports A1 across the grid; if the proportion at SEM 0.10 mm is under half, P1 is refuted for that scenario and the conclusion narrows to a reporting finding.
Explanations 3 to 5: differential error, selective reporting, and unit-of-analysis error. Arm-related geometry would show as association between the B5 features and larger effects (B6), but published reliability statistics cannot capture it, so the design can flag compatible features and not measure bias. Publication bias and selective outcome choice would inflate interpreted effects regardless of measurement; registration status is extracted but funnel-type analyses are not planned. Implants analyzed as independent despite clustering in patients create spuriously small standard errors, so unit of analysis is extracted as a covariate and sensitivity analysis.
6. Clinical and engineering implications
If the predictions hold, trial reports would benefit from three changes. First, a reliability statement reported in millimeters (SEM or SDC and the basis for it, namely re-reading or re-acquisition), following reporting guidance for reliability studies [20] and the principle that reliability should be reported alongside power [15]. Second, interpretation of group differences against an explicit anchor, with a statement of whether the anchor is the trial’s own. Third, restriction of individual-level language (progression, success, early-loss cut-off) to changes that exceed the SDC, or acknowledgment that the cut-off is a population-level discriminator.
For cut-offs, the conditional reading is that early loss of 0.44 to 0.5 mm [22, 23] sits close to the SDC for plausible SEM values; a prospective validation would need standardized, blinded, duplicate reads and a pre-specified threshold, and the reported outcome should be discrimination of later loss, not agreement of the individual measurement. The existing early-loss work comes from one center and a retrospective design [22, 23], and a recent independent retrospective study uses a different exposure definition [24].
For radiographic engineering, angular deviation of the receptor increases error in test-stand experiments [11] and the calibration reference affects accuracy [12]; individualized holders, geometric references in each film and allocation-blind rejection of non-readable films would address both random and differential error.
For meta-analysts, pooled differences of 0.05 mm [28, 29] require an error budget and an MID before clinical interpretation, and disagreement among syntheses of the same trials, as for crestal versus subcrestal placement [32–34], may partly reflect how loss is referenced and the error each trial carries.
7. Limitations
- No data. Every audit result is a prediction. The computations in Tables 2 and 3, the misclassification figures and the trial simulation use assumed parameters (a between-implant SD of 0.8 mm for the ICC route, a true-change SD of 0.5 mm, a normal distribution of true six-month change with mean 0.4 and SD 0.4 mm, independent errors at two occasions). Real MBL change is right-skewed and errors may be correlated across occasions or scale with the true value, which would change the numbers.
- Scenario benchmark, not measured error. The SEM grid is a bracket derived from a narrative statement of error [1], an implied value from one mini-implant study whose formula was not verified [10], and examiner variation in unfavorable settings [5]. If trials are in fact calibrated to an SEM below 0.1 mm, the main finding of H3 will narrow to a reporting and anchoring result.
- Abstract-level appraisal. All studies were appraised from PubMed abstracts retrieved on 17 November 2026. Several statements (for example, the mean underestimation reported by Christiaens and colleagues [6], and the conclusions of Walton and Layton [4]) come from the notes of this project and need full-text verification. The effect magnitudes in Section 2.5 are cited from the notes and abstracts and come mainly from syntheses and observational designs.
- Databases not accessible. Embase, Scopus and Web of Science were not available; the originality check relied on PubMed, Europe PMC and ClinicalTrials.gov, and several search phrases returned no records. A missed audit is therefore possible. In particular, a study combining effect sizes and error in a non-dental or grey-literature source would not have been found.
- Reference standard problem. Surgical measurements are themselves error-prone; the validity of radiographic MBL against histology or surgery is a separate question from reliability and is not resolved here [8, 13, 14].
8. Conclusions
Marginal bone level measured on intraoral radiographs carries measurement error that is small under calibrated, standardized reading and may be large in unselected settings. For randomized group comparisons, non-differential random error costs power and sample size but does not bias the contrast; differential systematic error and selective missing films can. For individual-level inference, such as a progression call or an early-loss cut-off of about 0.5 mm, the SDC is the relevant yardstick and may be of similar size. Whether differences of a few tenths of a millimeter matter to patients is a separate question that needs an anchored MID, which has not been established. The proposed audit would test, on a defined random sample of trials, whether interpreted effects sit below the benchmarks and whether reliability is reported in millimeters. Its predictions can be refuted, and the protocol is useful whichever way they fall, because it separates variance, bias, individual detectability and clinical meaning.
Cite this paper
Jain S, Gupta A. Smaller Than the Ruler: Radiographic Marginal Bone Level Measurement Error Versus the Effect Sizes Claimed in Implant Trials — A Meta-Research Protocol. Working paper. Center for Implant Dentistry; 2026. Available from: https://bayareaimplantdentistry.com/clinician-research-and-publications/marginal-bone-level-measurement-error
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