Skip to main content

Is Accelerating Bone Loss in Peri-Implantitis Real? Selection on the Outcome as an Alternative Explanation

Paper type
Methodological Study (theoretical, with simulation)
Status
Original Work · Working Paper
Keywords:
peri-implantitis · marginal bone loss · selection bias · regression to the mean · growth models · measurement error · simulation
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 methodological implications
  7. 7Limitations
  8. 8Conclusions

Abstract

Background. Peri-implantitis is widely described as progressing in a non-linear, accelerating pattern. This description rests largely on multilevel growth models fitted to implants that had already been identified as affected. Selecting implants on their final bone level conditions on the outcome and could, in principle, make earlier values look smaller and the trajectory look convex.

Objective and hypothesis. We hypothesized that some or all of the reported acceleration is an artefact of selection on the outcome, measurement error, and unequal observation intervals, and that only unselected, prospectively followed cohorts can establish the true shape.

Proposed approach. We state the selection mechanism formally, and we ran a Monte Carlo simulation (500,000 implants per scenario, assumed parameters) of four non-accelerating trajectory models, selecting implants whose observed final loss exceeded a cutoff. We then specify the analysis that an unselected cohort would require: pre-specified curvature tests in mixed-effects models, latent-class trajectories, and joint modeling of implant loss.

Expected contribution. The simulation partly refuted the hypothesis as first stated. Under linear random-effects and random-walk models, selection alone produced no curvature; curvature appeared only through measurement error at the selecting visit (apparent quadratic coefficients of 0.0004 to 0.0043 mm/yr^2 for error SDs of 0.15 to 0.50 mm), through a floor at zero loss, or through the mixing of onset times, and unequal follow-up produced deceleration instead. The artefact is therefore real but mechanism-specific and bounded, and the retrospective data cannot distinguish true acceleration from it. A leave-selection-visit-out analysis removes the endpoint component.

Conclusions. Acceleration of peri-implantitis bone loss is unproven rather than disproven. Claims about shape need unselected, prospectively followed implants, and case definitions that rely on thresholds without a baseline inherit the same identifiability problem. These are model-based conclusions under stated assumptions, not empirical findings.

1. Introduction

The statement that peri-implantitis progresses in a non-linear, accelerating manner appears in textbooks, consensus reports, and patient-facing arguments for early intervention. Its empirical basis is narrow. A multilevel growth model fitted to 105 implants in 62 patients with moderate or severe disease, identified from a 9-year follow-up of 596 randomly selected implant-carrying individuals, was reported to show a non-linear, accelerating pattern with onset mostly within 3 years of function [1]. An earlier analysis of 419 implants “with a history of bone loss” in 182 subjects reached the same qualitative conclusion about the rate of loss increasing over time [2]. The 2017 World Workshop review summarized this pattern as the expected course of the disease [3]. A later follow-up of a similarly labelled cohort of 182 patients, averaging 9.1 years, found only 0.3 mm of mean further loss at stable implants and an annual loss above 0.2 mm at 8.6% of implants [4]. Whether the cohorts in [2] and [4] are identical is not stated in the abstracts and cannot be confirmed here.

Two features of the supporting studies deserve scrutiny. First, the implants analyzed were identified because they ended with marked bone loss. Second, their earlier radiographs were then examined retrospectively. Any analysis that starts from the endpoint and looks backward is conditioned on the outcome. Conditioning on an outcome that is partly produced by random variation is a recognized route to bias, usually described as selection bias or, in the graphical language of causal inference, conditioning on a collider [5, 6]. Its most familiar consequence is regression to the mean: units chosen for extreme values tend to look less extreme on re-measurement. The question here is the converse one, that units chosen for extreme final values look less extreme before the end, and whether that can create the appearance of acceleration.

This manuscript examines that possibility in three steps. We state the selection mechanism with defined symbols and derive what it predicts for several families of non-accelerating trajectories. We then run a transparent Monte Carlo experiment to check the derivation and to size the artefact under stated assumptions. Finally, we specify the design and analysis that would let an unselected cohort answer the shape question, with numbered predictions and the results that would show acceleration to be real.

The analysis matters for two reasons beyond curve shape. Case definitions that apply a bone-level threshold without a baseline radiograph [7] condition on a final level in the same way, so their meaning for progression is entangled with the same issue. And the shape of progression determines how urgently an implant with moderate bone loss should be treated, which is a clinical claim that should not rest on an unverified inference.

We state at the outset that the simulation did not confirm the hypothesis in its simplest form. Section 3 reports what survived.

2. Background and critical appraisal of the evidence

Origin of the accelerating-progression claim

Fransson and colleagues examined all radiographs from the 1-year follow-up to the end-point examination (5 to 23 years) for 419 implants with a history of bone loss [2]. The mean bone loss after the first year was 1.68 mm, 32% of implants had lost 2 mm or more, and the multilevel model showed a non-linear pattern with an increasing rate over time. The time origin was year 1, the follow-up length differed widely between implants, and the entry criterion was a history of bone loss. Derks and colleagues used a comparable multilevel growth model for the 105 affected implants and derived the cumulative onset of disease from the estimated bone loss at each year [1]. The sampling frame was random, but the analyzed set was the affected subset. Both studies originate from one research group in Sweden, and the pattern has not, in the abstracts we retrieved, been independently replicated. The 2017 World Workshop review adopted the pattern [3], and a 2025 consensus summary on prevention and management of peri-implant diseases is the most recent consensus document we located [8]; we did not appraise how it treats the shape of progression.

Contradicting and qualifying evidence

The most direct contradiction comes from the follow-up of patients labelled as having progressive bone loss [4]. Fewer than one-third of those patients showed implant failure or an annual loss above 0.2 mm during follow-up, 3.1% of implants were lost, and treatment did not measurably change bone loss or failure. This is consistent with two readings that the abstract cannot separate: the original label overstated progression, or the label captured transient or measurement-driven extremes. A registry-based analysis of 70 patients diagnosed with moderate or severe disease 4 years earlier used Cox regression and mixed linear models to study further loss [9]; its mean loss of 1.1 mm with an SD of 2.0 mm over 3.3 years, as recorded in our candidate notes, implies strongly heterogeneous trajectories, though a standard deviation larger than the mean does not by itself identify the shape of any individual course.

Prospective data on early loss also complicate acceleration. A 10-year prospective cohort found that first-year loss of 0.5 mm or more raised the odds of later peri-implantitis roughly five-fold [10], and a retrospective study of 261 implants reported peri-implantitis in 63% of implants with bone loss before loading against 5% without it [11] (the abstract of that paper carries a correction notice dated March 2026, so its figures should be treated cautiously). If much of the eventual loss is determined early, a front-loaded pattern is at least as plausible as a late accelerating one. A prospective cohort of 73 patients and 322 implants reported an implant-level incidence of 9.4% over 3.9 years [12], which indicates that unselected cohorts contain few progressing implants, an important constraint on the sample size needed to study them.

Dependence of prevalence on definitions and thresholds

Reported prevalence of peri-implantitis ranges widely, and the thresholds used explain part of the spread [13, 14, 15]. In one Swedish sample the proportion with any peri-implantitis was 45%, compared with 14.5% for moderate or severe disease [16]. Re-applying the 2017 criteria to an existing cohort of 95 patients and 220 implants roughly halved the prevalence of peri-implantitis [17], examiner agreement in a reliability study was only moderate (kappa 0.50) [18], and the secondary, no-baseline definition has high specificity but low sensitivity against documented bone loss [7]. For the present question, the relevance is that a threshold on a final bone level, without a baseline, is a selection rule of exactly the type described above. Radiographic bone-level measurement itself carries error of its own [19], and an interpretation of early loss as a non-infectious remodeling response [20] means that early values are not interchangeable with later ones.

Precedent in periodontitis and trajectory modeling

The same debate occurred for periodontal attachment loss. The “burst” concept, usually traced to [21], holds that destruction occurs in episodes, in contrast to continuous linear progression. A multilevel analysis of longitudinal periodontal data found large negative correlations between the random linear and quadratic time coefficients; subjects and teeth with greater-than-average linear change experienced decelerated variation and the converse for those with less change, which the authors described as dynamic regression to the mean, and they proposed that burst and linear theories were manifestations of the same multilevel phenomenon [22]. This is the closest precedent we found. It concerns periodontal sites, not implants, and was not framed as selection on the outcome, but it establishes that apparent curvature in growth-model output can arise from the covariance structure of the data rather than from a biological acceleration. In the wider trajectory literature, reviews caution that latent-class and mixture trajectories depend on modeling assumptions and that class membership is not a discovered biological fact [23, 24], and joint models are recommended when dropout is informative [25].

Prospective evidence that favors acceleration

The evidence is not one-sided. A prospective study of 133 subjects with 407 implants, examined after about 5 years in function and again about 5 years later, reported that 13 implants in 7 subjects with progressive bone loss were removed between the second and third examinations, and that bone-level reduction was twice as great in the second interval as in the first [26]. Entry into that cohort did not depend on the outcome, so this is the strongest support for acceleration among the sources we retrieved. Three cautions apply. The abstract text we retrieved was truncated at the sentence reporting the doubling, so the set of implants it refers to must be checked in the full text. A comparison of two 5-year interval means cannot separate acceleration within implants from a growing share of progressing implants in the later interval. And the removal of 13 implants is informative loss, which a naive analysis of the remaining implants would handle poorly.

Originality check

We searched PubMed and Europe PMC using vocabularies of peri-implantitis progression, natural history, trajectories, regression to the mean, selection bias, collider bias, and periodontal burst versus linear models. We found no paper that applies selection-on-outcome or regression to the mean to the accelerating peri-implantitis claim. We cannot exclude that such an argument appears in a full text, a letter, or a source in the databases we could not access (Embase, Scopus, Web of Science). The periodontal precedent [22] and general selection-bias theory [5, 6] mean that the contribution here is the application, quantification, and design specification, not the underlying principle.

Table 1. Pivotal studies bearing on the shape of peri-implantitis bone loss (abstract-level appraisal).
StudyDesign and nMain finding relevant to shapeMain bias for the shape questionEvidence level
Fransson 2010 [2]Retrospective, 182 subjects, 419 implants with bone-loss historyRate of loss increased over timeSelected on outcome; unequal follow-up (5-23 y)B
Derks 2016 [1]Subset of 596 random patients; 62 patients, 105 implants modeledNon-linear accelerating loss; onset mostly within 3 yAffected subset only; quadratic form imposedB
Jemt 2015 [4]Follow-up of 182 “progressive” patients, mean 9.1 yMean further loss 0.3 mm; 8.6% of implants above 0.2 mm/yItself outcome-selected; treatment not randomizedB
Karlsson 2019 [9]Retrospective registry, 70 patientsMean loss 1.1 mm (SD 2.0) over 3.3 yRetrospective records; diagnosed-case entryC
Windael 2021 [10]Prospective, 407 patients, 1,482 implants, 10 yEarly loss predicts later diseaseThreshold-based outcome; early loss and onset confoundedB
Cecchinato 2014 [26]Prospective, 133 subjects, 407 implants, about 5 + 5 yBone-level reduction twice as great in the second interval; 13 implants removedTwo coarse intervals; informative removal; abstract truncatedB
Gilthorpe 2003 [22]Multilevel periodontal dataNegative linear-quadratic covariance; regression to the meanPeriodontal sites, not implantsC

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

3. Hypothesis and theoretical framework

Formal statement of the selection mechanism

Let Y_i(t) denote the true cumulative marginal bone loss (mm) of implant i at time t (years) after the 1-year reference radiograph, so that t=0 is the reference. Visits occur at t_j, j=0,…,J, with final visit time T=t_J. The recorded value is

Y_ij^*=Y_i(t_j)+ε_(ij),  ε_(ij)∼N(0,σ^2) independent,

where σ (mm) is the SD of radiographic measurement error, which includes projection, landmark identification, and calibration error [19]. A retrospective study of “affected” implants analyzes the subset with indicator

S_i=1{Y_iJ^*≥c},

where c (mm) is the cutoff, and then estimates the mean trajectory m_S(t_j)=E(Y_ij^*∣S_i=1). The unselected mean is m(t_j)=E(Y_ij^*). Apparent acceleration is summarized by two quantities: q, the coefficient of t^2 in a least-squares quadratic fit to the mean trajectory (mm/yr2), and R, the ratio of loss in the late half of follow-up to loss in the early half, R=(m(9)−m(5))/(m(4)−m(0)) for the ten annual visits used below, with R>1 indicating acceleration. We ask whether q_S and R_S for the selected set differ from q and R for all implants when the true trajectories are not accelerating.

The mechanism is conditioning on a descendant of both the true course and the error. Because S_i depends on Y_i(T)+ε_(iJ), selection tilts the distribution of every quantity that is correlated with that sum, which includes the earlier true values and the final error. This is the structure of selection bias in the epidemiologic literature [5, 6], and the change of earlier values in the opposite direction from the selection is regression to the mean.

What Gaussian selection predicts

If the true process and the error are jointly Gaussian, conditioning on Y_J^*≥c shifts the mean of any earlier observation by a multiple of the shift in the selecting variable:

E(Y_j^*∣S=1)=μ_j+κ_j δ,  κ_j=(Cov(Y_j^*,Y_J^*))/(Var(Y_J^*)),  δ=E(Y_J^*∣S=1)−μ_J,

where μ_j=E(Y_j^*). Three structures are relevant.

  • Linear trajectories with between-implant variation in level and slope, Y_i(t)=a_i+b_it with independent a_i (variance σ_a^2) and b_i (variance σ_b^2). For t_j<T, Cov(Y_j^*,Y_J^*)=σ_a^2+σ_b^2t_jT is linear in t_j, and so is κ_j. If μ_j is linear, the selected mean trajectory is linear. Selection raises the level and slope of the selected group but does not bend its mean curve.
  • A random walk with drift, with step SD s per year. Here Cov(Y_j,Y_J)=s^2t_j, again linear in t_j, and the selected mean is again linear (a discrete analogue of the Brownian bridge).
  • At the selecting visit itself, the selecting variable is the observation itself, so κ_J=1, whereas continuing the linear function of the earlier visits would give Var(Y_J)/Var(Y_J^*)=1−σ^2/Var(Y_J^*). The final recorded value is therefore elevated beyond the line followed by the earlier visits by

h=(σ^2)/(Var(Y_J^*)) δ,

the expected value of the selected error. A single raised final point on an otherwise linear mean looks like an upturn at the end of follow-up, and a quadratic fit assigns it a positive curvature of approximately q≈w h, where w is the least-squares weight of the last visit on the quadratic coefficient. For ten annual visits (t=0,…,9), w=0.02273 (computed, see Section 3.4).

Consequently, selection alone does not generate acceleration in the linear-Gaussian case. What it generates is a final-visit excess proportional to σ^2. This is a narrower conclusion than the hypothesis as first stated, and the simulation below quantifies it.

Mechanisms that are not Gaussian-linear

Curvature can arise through at least four additional routes, each of which we simulated.

  • A floor. Bone loss measured against a reference cannot, by convention or by reporting practice, be negative, so recorded early values near zero with error may be truncated at zero. Truncation raises small values and, with error, alters the shape of the mean.
  • Mixing of onset times. If each implant is stable until a personal onset time and then loses bone at a constant rate, no individual trajectory accelerates, but the average over implants with different onset times is convex, because the mean of hinge functions is convex. This is population-level convexity without individual acceleration, and it is the most biologically plausible way for an average to curve.
  • Unequal follow-up. If the final examination occurs at different times for different implants (the retrospective cohort in [2] spanned 5 to 23 years) and implants are selected on the value at their own final examination, the implants contributing at late times are a different mix from those contributing early. Selected implants with short follow-up must have steeper slopes to reach the cutoff, so the later portion of the mean is composed of shallower implants, which tends to produce deceleration.
  • Baseline referencing. If loss is computed relative to an observed baseline that carries error, the baseline error is shared by all later values of the same implant. Selection on high final loss then favors a negative baseline error, which lifts every later value of that implant and creates a small early step (a concave feature) that offsets part of the endpoint excess; the net effect in the simulation was negligible.

The second mechanism also bears on interpretation: even a correct convex population average does not demonstrate that individual implants accelerate. The retrospective growth models reported both implant- and patient-level random effects [1, 2]; the quadratic term in such models is a fixed effect on the population average plus random deviations, and its sign does not identify individual acceleration without further assumptions, a point that parallels the burst-versus-linear resolution in periodontal data [22].

Illustrative computation under stated assumptions — not empirical data

The script sim_selection.py (saved in the paper folder, with sim_extra.py) generated, for each scenario, 10 independent batches of 50,000 implants (500,000 per scenario) with annual visits at t=0,…,9 years. All parameters are assumptions chosen for plausibility, not estimated from data. Model A (linear): a_i∼N(0,0.30^2) mm, b_i∼N(0.15,0.15^2) mm/yr truncated at zero. Model B (random walk): drift 0.10 mm/yr, step SD 0.25 mm/yr. Model D (hinge): 40% of implants progress, onset uniform on 0 to 8 years, constant rate after onset with lognormal distribution (median 0.30 mm/yr, SD of log 0.5), the remaining 60% stable. Model G is model A with recorded loss truncated at zero. Model F is model A with the final visit at a random time among visits 4 to 9 and selection on the value at that visit. Measurement error σ∈{0,0.15,0.30,0.50,0.80} mm was applied independently at each visit, and the main cutoff was c=2.0 mm on the observed final value. For each batch we computed q and R for the selected and for all implants and report the mean and the SD across batches (a Monte Carlo variability, not a sampling distribution of a cohort).

Table 2. Simulation results for selection on observed final loss of 2.0 mm or more. Mean of 10 batches of 50,000 implants; q in mm/yr2 (mean ± SD across batches); R = late/early loss ratio. Illustrative computation under stated assumptions; not empirical data.
Scenarioσ (mm)q, all implantsR, allq, selectedR, selectedSelected per batch
A linear0.00-0.0000 ± 0.00001.000+0.0000 ± 0.00001.00015,941
A linear0.30+0.0000 ± 0.00011.000+0.0017 ± 0.00011.06016,120
B random walk0.00-0.0000 ± 0.00010.996-0.0001 ± 0.00030.9963,570
B random walk0.30-0.0000 ± 0.00010.997+0.0046 ± 0.00041.2074,349
D onset hinge0.00+0.0083 ± 0.00013.429+0.0264 ± 0.00032.2336,140
D onset hinge0.30+0.0083 ± 0.00013.414+0.0279 ± 0.00042.3556,314
G linear, floor at 00.00+0.0021 ± 0.00001.152+0.0020 ± 0.00001.07215,941
G linear, floor at 00.30+0.0027 ± 0.00011.207+0.0050 ± 0.00011.18816,120
F unequal follow-up0.00-0.0001 ± 0.00030.997-0.0076 ± 0.00030.7798,075
F unequal follow-up0.30-0.0001 ± 0.00030.994-0.0054 ± 0.00040.8378,515
A, baseline-referenced0.30+0.0000 ± 0.00011.000+0.0001 ± 0.00011.00216,116

The simulated results follow the algebra. In the baseline-referenced variant, q in the selected group stayed at or below +0.0001 mm/yr2 for every σ from 0 to 0.80 mm (sim_output.txt, Table 6). With no measurement error, selection on the final value of the linear and random-walk models left q at zero within Monte Carlo variability (Table 2, rows with σ=0). With σ=0.30 mm, the selected group had a small positive q (+0.0017 mm/yr2 for model A, +0.0046 for the random walk) and R of 1.06 and 1.21. In model D the all-implant mean was already strongly convex (R=3.4) although no implant accelerates, and selection reduced rather than created the apparent acceleration. In model G the floor produced a positive q and R>1 in the unselected set. In model F the selected group showed deceleration (R<1).

The analytic endpoint formula agreed with the simulation. For model A at c=2.0 mm, using the Gaussian approximation with μ_J=1.35 mm, Var(Y_J^*)=0.09+0.0225×81+σ^2 mm2 (this ignores the truncation of slopes), the predicted q was 0.0004, 0.0016, and 0.0042 mm/yr2 for σ=0.15, 0.30, and 0.50 mm. The simulated values were +0.0004, +0.0016, and +0.0043 (the all-visits column in sim_extra_output.txt). Excluding the selecting visit from the curvature fit (visits 0 to 8 only) gave q of +0.0000, +0.0000, and +0.0000 for model A and -0.0001, -0.0001, and -0.0002 for the random walk at the same three error levels, so the endpoint component is removable by design.

Table 3. Sensitivity grid: apparent curvature q (mm/yr2) in the selected group for models A (linear) and B (random walk), by cutoff c and error SD σ. Mean over 10 batches; SD across batches ranged up to 0.0019 (largest for the random walk at c = 3.0; full output in sim_output.txt). Illustrative computation; not empirical data.
Model, cutoff c (mm)σ = 0σ = 0.15σ = 0.30σ = 0.50σ = 0.80
A, c = 0.5-0.0000+0.0002+0.0008+0.0022+0.0050
A, c = 1.0-0.0000+0.0003+0.0010+0.0027+0.0065
A, c = 2.0+0.0000+0.0004+0.0017+0.0044+0.0101
A, c = 3.0+0.0000+0.0006+0.0024+0.0063+0.0143
B, c = 0.5-0.0000+0.0003+0.0013+0.0033+0.0077
B, c = 1.0-0.0000+0.0006+0.0022+0.0054+0.0113
B, c = 2.0-0.0001+0.0012+0.0046+0.0106+0.0203
B, c = 3.0-0.0001+0.0017+0.0071+0.0172+0.0309

The grid shows that apparent curvature rises with both the cutoff and the error SD. To judge the size, a coefficient of 0.010 mm/yr2 corresponds to an extra 0.81 mm of loss at year 9 relative to a straight line through the origin (0.010×81). Under these assumptions the artefact of selection and error reaches that size only at the larger error SDs: for the random walk with σ≥0.50 mm and c≥2.0 mm, or with σ=0.80 mm and c≥1.0 mm, and for the linear model only with σ=0.80 mm and c≥2.0 mm. Whether such error SDs are realistic for radiographic bone levels is not established here. The floor model (G) produced selected q between 0.0026 and 0.0210 and R between 1.07 and 1.81 across the grid we ran, with larger values at larger σ, because the floor acts at the early visits regardless of selection.

Hypothesis, as narrowed

The original hypothesis (selection on the outcome by itself produces apparent acceleration) is not supported in linear-Gaussian trajectories. The surviving hypothesis has four parts.

H1. In outcome-selected cohorts, the curvature estimated at the selecting visit is biased upward in proportion to σ^2, and the bias is removable by excluding that visit. H2. Floors, truncation, and conventions that discard negative loss create apparent acceleration independently of selection. H3. Population-average convexity can arise from heterogeneity in onset time without any individual acceleration, so the retrospective growth-model curvature is not evidence about the course of an individual implant. H4. With unequal follow-up, selection on final value can produce deceleration, so the sign of the bias is design-dependent, and the direction of the published pattern cannot be inferred without knowing the follow-up distribution.

Numbered predictions and results that would refute them

P1. In any dataset of outcome-selected implants, the curvature estimate will fall toward zero, or change sign, when the selecting visit is excluded. Refuted if curvature is unchanged after exclusion.

P2. In an unselected cohort, the average annual bone loss of the implants that later cross a diagnostic threshold will not rise across the years before crossing once recorded loss is not truncated at zero. Refuted if late-interval loss exceeds early-interval loss by a margin larger than the measurement error.

P3. Within individual implants that progress, the within-implant rate (estimated from at least five visits after onset) will be approximately constant, with population convexity attributable to variation in onset. Refuted if within-implant rate increases with time since onset.

P4. Re-estimating the published models after restricting to a common follow-up window and aligning time on a pre-specified origin (not on the final examination) will reduce the reported curvature. Refuted if curvature persists unchanged.

P5. Further loss after labelling will be smaller, on average, than the loss predicted by extrapolating the retrospective growth curve, as in the follow-up of the “progressive” cohort [4]. Refuted if observed further loss equals or exceeds the extrapolation.

P6. The share of implants with rising annual loss in unselected data will be a minority of the affected implants. The accelerating-majority claim is refuted if latent-class analysis finds that most affected implants belong to a class with positive curvature that exceeds measurement error.

Results that would show acceleration is real: a positive, pre-specified curvature in an unselected cohort that persists when the selecting visit is excluded, that exceeds the error-based bias bound in Section 4, that appears within individual implants (not only in the average), and that is robust to informative loss of implants.

4. Proposed methodology

The design below is a specification for a future study. No cohort has been recruited, no data have been analyzed, and no ethics approval or registration is claimed.

Design and population

The cleanest design is an inception cohort of implants followed prospectively with scheduled radiographs, so that the shape of the trajectory is estimated before anyone knows which implants will become cases. Eligible implants would be those placed in a defined clinical program, with a standardized radiograph at prosthesis delivery, at the 1-year reference visit, and annually thereafter for at least 8 years. The same design can be realized retrospectively in a registry or a practice-based database with dated, calibrated radiographs if three conditions hold: all implants of a defined placement cohort are included whether or not they later develop disease; the denominator is fixed before outcomes are examined; and implants lost or removed are retained in the dataset with their dates and reasons. The target population is all implants in the inception cohort, with a pre-specified secondary population of implants that cross a diagnostic threshold during follow-up.

An alternative that already exists in several research groups is re-analysis of data collected for incidence studies, such as the prospective cohort of 322 implants followed for 3.9 years [12] or the 10-year prospective cohort of 1,482 implants [10]. Both would need annual radiographs and an unaltered record of all implants. We have not verified that either has the required structure.

Measurements and their validity

The outcome is marginal bone level on standardized intraoral radiographs relative to a fixed implant landmark, measured at mesial and distal sites. Radiographic methods differ somewhat in measurement accuracy [19], so the protocol would require (i) calibration to a known implant dimension on every image, (ii) duplicate blinded readings by two examiners on a random subset of at least 10% of images to estimate σ and its dependence on bone level, (iii) readers blinded to visit order and case status, and (iv) recording of negative values (apparent gain) without truncation, so that the floor mechanism does not operate. Clinical covariates (probing depth, bleeding, suppuration) would be recorded as time-varying variables, with the case definitions of the 2017 consensus [27, 28] applied after the fact for comparison with earlier studies but never used for entry into the analysis of shape.

Pre-specified analysis of curvature

The primary model is a mixed-effects growth model for implant i nested in patient k:

Y_ikj^*=β_0+β_1t_(ij)+β_2t_ij^2+u_(0k)+u_(1k)t_(ij)+v_(0i)+v_(1i)t_(ij)+v_(2i)t_ij^2+ε_(ikj),

with random effects for patient and implant, an unstructured covariance among implant-level effects, and residual variance estimated from the duplicate-reading substudy and not left free. The primary estimand is β_2 (mm/yr2) with a pre-specified margin: acceleration would be declared only if the lower 95% confidence limit of β_2 exceeds the error-based bias bound w h from Section 3.2, evaluated at the observed σ and at the cutoff of any selection that was applied. A pre-specified sensitivity analysis excludes the visit that defines any case threshold. Because a quadratic form imposes curvature, a second model uses natural cubic splines or fractional polynomials and compares the quadratic to the linear model by likelihood ratio, with an information criterion reported.

Because the covariance between random linear and quadratic terms is informative about regression to the mean, as shown for periodontal data [22], the model would report the correlation between v_(1i) and v_(2i) and the variance of v_(2i). A strongly negative correlation alone would be treated as a warning about covariance structure, not as evidence of acceleration or deceleration.

Distinguishing individual acceleration from mixed onset

To separate H3 from true individual acceleration, the study would fit (a) a change-point model in which each implant has a personal onset time and a constant post-onset rate, (b) a model in which the post-onset rate depends on time since onset, and (c) a latent-class growth model with classes allowed to differ in slope and curvature. Latent-class and mixture models require assumptions about within-class distributions, and the classes they return should not be treated as discovered biological entities [23, 24]. The comparison of (a) with (b) is the key test: individual acceleration requires that the post-onset rate term be positive and larger than the error-based bound, whereas population convexity from mixed onsets does not.

Informative loss and treatment

Implants removed for severe bone loss, and implants whose treatment changes the subsequent course, leave the observed process in a way related to the outcome. Both can bias estimated curvature, since the highest-loss implants disappear and treated implants stop progressing. The proposed approach is a joint model linking the longitudinal bone-level submodel to a time-to-event submodel for implant removal and for first treatment, with shared random effects, as used for informative dropout in other disease areas [25]. Treatment would also enter the longitudinal submodel as a time-varying covariate. The curvature estimate from the joint model would be compared with the naive mixed model, and a difference larger than the confidence interval would be reported as evidence of informative censoring. In the follow-up of “progressive” cohorts, treatment did not measurably change bone loss or implant failure [4], which suggests the correction may be small, but the observational nature of that finding does not exclude confounding by indication.

Sample size

The sample-size reasoning is for the primary curvature test, treated as a two-stage analysis for planning purposes. Each implant’s quadratic coefficient is estimated by ordinary least squares from ten annual visits; its sampling variance is σ^2v with v=0.001894 (the (3,3) element of (X^⊤X)^(−1) for t=0,…,9, computed). The between-implant SD of true curvature is σ_q. The number of independent implants needed to detect a mean curvature q with two-sided α=0.05 and power 0.80 is

n=((z_(0.975)+z_(0.80))^2 (σ_q^2+σ^2v))/(q^2),

with (1.960+0.842)^2=7.849. Clustering of implants within patients was handled with a design effect 1+(m−1)ρ, assuming m=2.5 implants per patient and an intraclass correlation ρ=0.5 (both assumptions), giving 1.75. Computed values (sim_extra.py): For σ=0.30 mm, σ_q=0.01 mm/yr2 and q=0.010, 22 independent implants, or 38 clustered implants from 15 patients. For the same σ and σ_q with q=0.005, 85 independent and 149 clustered implants (60 patients). For σ=0.50, σ_q=0.02, q=0.005, 275 independent and 480 clustered implants (192 patients). A simulation of 2,000 replicates with 200 independent implants, σ=0.30, σ_q=0.01 and true q=0.010 gave a power of 1.000, consistent with the formula, which predicts that 22 would suffice.

These numbers refer to implants that are in the analyzable curved class. In an unselected cohort most implants do not progress; incidences of about 9% have been reported for implant-level peri-implantitis over 3.9 years [12], and 8.6% of implants in the “progressive” cohort lost more than 0.2 mm per year [4]. If about 10% of implants are informative for curvature, the 149 clustered affected implants of the second example correspond to roughly 1,490 implants in total, or about 596 patients at 2.5 implants per patient. That arithmetic is conditional on an assumed 10% and would need to be recomputed from pilot data. If the class of affected implants is defined from the same data used to estimate curvature, the analysis is again outcome-selected. The remedy proposed here is sample splitting by visit: class membership is determined from the odd-numbered visits and curvature is estimated from the even-numbered visits, which removes the shared error, though not any dependence through the true trajectory.

Bias control, ethics and feasibility

Controls built into the design are: the all-implant analysis alongside any selected-subgroup analysis; a measurement-error substudy; exclusion of the selecting visit; a fixed observation window common to all implants (to avoid composition change as in model F); a pre-registered analysis plan before data are examined; and sensitivity analyses across the cutoff and σ grid of Table 3. A prospective cohort would need ethics review and informed consent, and a retrospective registry study would need data-governance approval; neither has been sought. Feasibility is limited by the need for long follow-up with regular radiographs, by the small proportion of progressing implants, and by the fact that patients with severe bone loss are treated, which limits observation of untreated courses.

The study design is summarized in Figure 2.

5. Competing explanations and how the design discriminates among them

Four explanations for a convex average curve in outcome-selected data need to be separated.

E1. Selection plus measurement error. The predicted signature is a curvature concentrated in the final visit and proportional to σ^2, and it should vanish when the selecting visit is excluded (P1). It also scales with the cutoff, which can be tested by re-estimating at several cutoffs.

E2. Floors and truncation. The signature is curvature that exists in the unselected group too (as in model G) and depends on whether negative values were retained. The design discriminates by recording untruncated values and comparing.

E3. Mixed onset without individual acceleration. The signature is a convex average with a constant post-onset rate for each implant. The change-point comparison of Section 4.4 discriminates it from E4.

E4. True individual acceleration. The signature is a rising post-onset rate within implants that persists with the selecting visit excluded, exceeds the error bound, and survives joint modeling of removal. A biologic mechanism might include positive feedback between bone loss, surface exposure, and biofilm accumulation, but the evidence that early loss is the stronger predictor [10, 11] and that early loss may be non-infectious remodeling [20] leaves room for front-loaded alternatives.

An additional alternative is that the entry labels themselves are wrong, so that the selection is on a noisy classification, not on the true course. Examiner agreement is only moderate in at least one reliability study [18], so misclassification can inject additional selection on noise.

The design does not discriminate cleanly in two situations. If measurement error is correlated across visits within an implant (for example, from a persistently distorted projection geometry), the Gaussian derivation changes, and a modified bound would be needed. And if treatment or removal depends on the same unobserved severity that drives the loss, the joint model corrects only for what it models.

6. Clinical and methodological implications

These are conditional on the simulation assumptions and on verification in real data.

If the retrospective convexity is largely an artefact or a mixed-onset average, statements that peri-implantitis accelerates should be worded as hypotheses, and the urgency of intervention for an implant with moderate bone loss should be argued from observed unselected outcomes, such as the proportion that go on to lose substantial bone, not from the shape of a retrospective curve. The follow-up of the “progressive” cohort [4], in which most implants lost little further bone, would be consistent with this, although it was itself an outcome-selected cohort and does not by itself settle the question.

For case definitions, a threshold on final bone level without a baseline is, by construction, a selection rule on the outcome. The secondary definition has high specificity and low sensitivity against documented bone loss [7], and prevalence in the same sample depends strongly on the threshold [16]. A university-based sample reported a patient-level prevalence of 56.6% [29], and pooled prevalence and incidence estimates are available from systematic reviews [30], so threshold-based cases are numerous enough that definitional selection matters at scale. The practical implication for trial design is that eligibility criteria should state whether bone loss is measured against a recorded baseline, and that trials should not infer the natural history of the control arm from the shape of the pre-enrollment curve.

For measurement, the analysis argues for reporting the measurement-error SD of bone-level readings in every longitudinal study, because it enters the bias bound directly.

7. Limitations

The simulation is a statement about a model, not about implants. Every parameter (slope SD, offset SD, error SD, onset distribution, 40% progressing fraction, step SD of the random walk) is an assumption, and none was estimated from the cohorts discussed. Measurement error was taken as Gaussian, independent across visits, and constant across bone levels; real radiographic error may be heteroscedastic, correlated within an implant, and may include systematic projection bias. The retrospective studies we criticize used multilevel models with structures more complex than the ones simulated, and we did not reproduce their analyses; our results show what selection and error can do in simple models, not what they did in those studies. We also do not know the follow-up distribution, the exact selection rule, or the visit schedule in those studies beyond the abstract-level information cited, and the rule of selection in [1] was based on a classification at the end of follow-up, which our single-cutoff rule approximates only roughly.

Evidence appraisal was at abstract level; we did not read full texts and may have missed relevant methodological detail, including adjustments that address the issues raised here. It is possible that the original authors accounted for selection in ways not visible in the abstracts. Embase, Scopus, and Web of Science were not accessible, and our originality search could miss relevant sources. The statement that the cohorts in [2] and [4] may overlap is unverified.

The simulation covers one outcome, bone loss, and one kind of selection. It says nothing about the biological plausibility of acceleration, and its finding that selection alone yields small curvature cuts both ways: it weakens the case that the published acceleration is mostly an artefact of selection, while leaving it unproven. The sample-size arithmetic is based on a two-stage approximation that ignores missing visits and unequal intervals; a simulation-based calculation using the full mixed model would be required.

8. Conclusions

The claim that peri-implantitis bone loss accelerates is mainly supported by retrospective multilevel models fitted to implants chosen for their outcome. Our analysis under stated assumptions shows that selection on the final value does not bend the mean trajectory of linear or random-walk processes; it adds an endpoint excess proportional to the measurement error variance, which can be removed by design. Larger apparent acceleration can arise from floors on recorded loss and from averaging over implants with different onset times, and unequal follow-up can push the bias in the opposite direction. A prospective cohort not selected on outcome did report greater loss in a later interval [26], which keeps true acceleration a live possibility. The published pattern therefore cannot be read as demonstrating individual acceleration, and it cannot be dismissed as an artefact either. Resolving the question requires unselected, prospectively followed implants, untruncated and error-characterized measurements, a pre-specified curvature test with a bias margin, change-point and latent-class comparisons to separate mixed onset from true acceleration, and joint modeling of implant removal and treatment.

Cite this paper

Jain S, Gupta A. Is Accelerating Bone Loss in Peri-Implantitis Real? Selection on the Outcome as an Alternative Explanation. Working paper. Center for Implant Dentistry; 2026. Available from: https://bayareaimplantdentistry.com/clinician-research-and-publications/peri-implantitis-acceleration-selection-artefact

References

  1. Derks J, Schaller D, Håkansson J, Wennström JL, Tomasi C, Berglundh T. Peri-implantitis - onset and pattern of progression. J Clin Periodontol. 2016;43(4):383-8. doi:10.1111/jcpe.12535 (opens in a new tab). PMID: 26900869 (opens in a new tab).
  2. Fransson C, Tomasi C, Pikner SS, Gröndahl K, Wennström JL, Leyland AH, et al. Severity and pattern of peri-implantitis-associated bone loss. J Clin Periodontol. 2010;37(5):442-8. doi:10.1111/j.1600-051X.2010.01537.x (opens in a new tab). PMID: 20507368 (opens in a new tab).
  3. Schwarz F, Derks J, Monje A, Wang HL. Peri-implantitis. J Clin Periodontol. 2018;45 Suppl 20:S246-S266. doi:10.1111/jcpe.12954 (opens in a new tab). PMID: 29926484 (opens in a new tab).
  4. Jemt T, Sundén Pikner S, Gröndahl K. Changes of Marginal Bone Level in Patients with “Progressive Bone Loss” at Brånemark System® Implants: A Radiographic Follow-Up Study over an Average of 9 Years. Clin Implant Dent Relat Res. 2015;17(4):619-28. doi:10.1111/cid.12166 (opens in a new tab). PMID: 24172070 (opens in a new tab).
  5. Hernán MA, Hernández-Díaz S, Robins JM. A structural approach to selection bias. Epidemiology. 2004;15(5):615-25. doi:10.1097/01.ede.0000135174.63482.43 (opens in a new tab). PMID: 15308962 (opens in a new tab).
  6. Westreich D. Berkson’s bias, selection bias, and missing data. Epidemiology. 2012;23(1):159-64. doi:10.1097/EDE.0b013e31823b6296 (opens in a new tab). PMID: 22081062 (opens in a new tab).
  7. Romandini M, Berglundh J, Derks J, Sanz M, Berglundh T. Diagnosis of peri-implantitis in the absence of baseline data: A diagnostic accuracy study. Clin Oral Implants Res. 2021;32(3):297-313. doi:10.1111/clr.13700 (opens in a new tab). PMID: 33340418 (opens in a new tab).
  8. Wang HL, Avila-Ortiz G, Monje A, Kumar P, Calatrava J, Aghaloo T, et al. AO/AAP consensus on prevention and management of peri-implant diseases and conditions: Summary report. J Periodontol. 2025;96(6):519-541. doi:10.1002/JPER.25-0270 (opens in a new tab). PMID: 40501397 (opens in a new tab).
  9. Karlsson K, Derks J, Håkansson J, Wennström JL, Petzold M, Berglundh T. Interventions for peri-implantitis and their effects on further bone loss: A retrospective analysis of a registry-based cohort. J Clin Periodontol. 2019;46(8):872-879. doi:10.1111/jcpe.13129 (opens in a new tab). PMID: 31077421 (opens in a new tab).
  10. Windael S, Collaert B, De Buyser S, De Bruyn H, Vervaeke S. Early peri-implant bone loss as a predictor for peri-implantitis: A 10-year prospective cohort study. Clin Implant Dent Relat Res. 2021;23(3):298-308. doi:10.1111/cid.13000 (opens in a new tab). PMID: 34076941 (opens in a new tab).
  11. Moser D, Ozgur E, Tjokro J, Raabe C, Chappuis V, Avila-Ortiz G, et al. Effect of Early Radiographic Bone Loss Before Loading on Implant-Related Outcomes: A Long-Term Retrospective Study. Clin Oral Implants Res. 2026;37(6):704-713. doi:10.1111/clr.70112 (opens in a new tab). PMID: 41742397 (opens in a new tab).
  12. Romandini M, Lima C, Banaco D, Azevedo R, Sanz M. Incidence and Risk Factors of Peri-Implantitis Over Time-A Prospective Cohort Study. J Periodontal Res. 2025;60(12):1222-1236. doi:10.1111/jre.13367 (opens in a new tab). PMID: 39803810 (opens in a new tab).
  13. Derks J, Tomasi C. Peri-implant health and disease. A systematic review of current epidemiology. J Clin Periodontol. 2015;42 Suppl 16:S158-71. doi:10.1111/jcpe.12334 (opens in a new tab). PMID: 25495683 (opens in a new tab).
  14. Rakic M, Galindo-Moreno P, Monje A, Radovanovic S, Wang HL, Cochran D, et al. How frequent does peri-implantitis occur? A systematic review and meta-analysis. Clin Oral Investig. 2018;22(4):1805-1816. doi:10.1007/s00784-017-2276-y (opens in a new tab). PMID: 29218422 (opens in a new tab).
  15. Diaz P, Gonzalo E, Villagra LJG, Miegimolle B, Suarez MJ. What is the prevalence of peri-implantitis? A systematic review and meta-analysis. BMC Oral Health. 2022;22(1):449. doi:10.1186/s12903-022-02493-8 (opens in a new tab). PMID: 36261829 (opens in a new tab).
  16. Derks J, Schaller D, Håkansson J, Wennström JL, Tomasi C, Berglundh T. Effectiveness of Implant Therapy Analyzed in a Swedish Population: Prevalence of Peri-implantitis. J Dent Res. 2016;95(1):43-9. doi:10.1177/0022034515608832 (opens in a new tab). PMID: 26701919 (opens in a new tab).
  17. Shimchuk AA, Weinstein BF, Daubert DM. The impact of a change in classification criteria on the prevalence of peri-implantitis: A cross-sectional analysis. J Periodontol. 2021;92(9):1339-1346. doi:10.1002/JPER.20-0566 (opens in a new tab). PMID: 33277941 (opens in a new tab).
  18. Marini L, Tomasi C, Gianserra R, Graziani F, Landi L, Merli M, et al. Reliability assessment of the 2018 classification case definitions of peri-implant health, peri-implant mucositis, and peri-implantitis. J Periodontol. 2023;94(12):1461-1474. doi:10.1002/JPER.23-0129 (opens in a new tab). PMID: 37322858 (opens in a new tab).
  19. De Smet E, Jacobs R, Gijbels F, Naert I. The accuracy and reliability of radiographic methods for the assessment of marginal bone level around oral implants. Dentomaxillofac Radiol. 2002;31(3):176-81. doi:10.1038/sj/dmfr/4600694 (opens in a new tab). PMID: 12058265 (opens in a new tab).
  20. Albrektsson T, Dahlin C, Jemt T, Sennerby L, Turri A, Wennerberg A. Is marginal bone loss around oral implants the result of a provoked foreign body reaction?. Clin Implant Dent Relat Res. 2014;16(2):155-65. doi:10.1111/cid.12142 (opens in a new tab). PMID: 24004092 (opens in a new tab).
  21. Socransky SS, Haffajee AD, Goodson JM, Lindhe J. New concepts of destructive periodontal disease. J Clin Periodontol. 1984;11(1):21-32. doi:10.1111/j.1600-051x.1984.tb01305.x (opens in a new tab). PMID: 6582072 (opens in a new tab).
  22. Gilthorpe MS, Zamzuri AT, Griffiths GS, Maddick IH, Eaton KA, Johnson NW. Unification of the “burst” and “linear” theories of periodontal disease progression: a multilevel manifestation of the same phenomenon. J Dent Res. 2003;82(3):200-5. doi:10.1177/154405910308200310 (opens in a new tab). PMID: 12598549 (opens in a new tab).
  23. Herle M, Micali N, Abdulkadir M, Loos R, Bryant-Waugh R, Hübel C, et al. Identifying typical trajectories in longitudinal data: modelling strategies and interpretations. Eur J Epidemiol. 2020;35(3):205-222. doi:10.1007/s10654-020-00615-6 (opens in a new tab). PMID: 32140937 (opens in a new tab).
  24. Lennon H, Kelly S, Sperrin M, Buchan I, Cross AJ, Leitzmann M, et al. Framework to construct and interpret latent class trajectory modelling. BMJ Open. 2018;8(7):e020683. doi:10.1136/bmjopen-2017-020683 (opens in a new tab). PMID: 29982203 (opens in a new tab).
  25. Saulnier T, Philipps V, Meissner WG, Rascol O, Pavy-Le Traon A, Foubert-Samier A, et al. Joint models for the longitudinal analysis of measurement scales in the presence of informative dropout. Methods. 2022;203:142-151. doi:10.1016/j.ymeth.2022.03.003 (opens in a new tab). PMID: 35283328 (opens in a new tab).
  26. Cecchinato D, Parpaiola A, Lindhe J. Mucosal inflammation and incidence of crestal bone loss among implant patients: a 10-year study. Clin Oral Implants Res. 2014;25(7):791-6. doi:10.1111/clr.12209 (opens in a new tab). PMID: 23763507 (opens in a new tab).
  27. Berglundh T, Armitage G, Araujo MG, Avila-Ortiz G, Blanco J, Camargo PM, et al. Peri-implant diseases and conditions: Consensus report of workgroup 4 of the 2017 World Workshop on the Classification of Periodontal and Peri-Implant Diseases and Conditions. J Clin Periodontol. 2018;45 Suppl 20:S286-S291. doi:10.1111/jcpe.12957 (opens in a new tab). PMID: 29926491 (opens in a new tab).
  28. Renvert S, Persson GR, Pirih FQ, Camargo PM. Peri-implant health, peri-implant mucositis, and peri-implantitis: Case definitions and diagnostic considerations. J Clin Periodontol. 2018;45 Suppl 20:S278-S285. doi:10.1111/jcpe.12956 (opens in a new tab). PMID: 29926496 (opens in a new tab).
  29. Romandini M, Lima C, Pedrinaci I, Araoz A, Soldini MC, Sanz M. Prevalence and risk/protective indicators of peri-implant diseases: A university-representative cross-sectional study. Clin Oral Implants Res. 2021;32(1):112-122. doi:10.1111/clr.13684 (opens in a new tab). PMID: 33210772 (opens in a new tab).
  30. Galarraga-Vinueza ME, Pagni S, Finkelman M, Schoenbaum T, Chambrone L. Prevalence, incidence, systemic, behavioral, and patient-related risk factors and indicators for peri-implant diseases: An AO/AAP  systematic review and meta-analysis. J Periodontol. 2025;96(6):587-633. doi:10.1002/JPER.24-0154 (opens in a new tab). PMID: 40489307 (opens in a new tab).