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Why Do Implant Failures Cluster in Patients? A Frailty-Model Framework to Separate Host, Operator, and Chance

Paper type
Methodological Study (theoretical, with illustrative simulation)
Status
Original Work · Working Paper
Keywords:
dental implants · clustering · intraclass correlation · frailty model · design effect · operator effect
Contents
  1. 1Introduction
  2. 2Background and critical appraisal of the evidence
  3. 3Hypothesis and theoretical framework
  4. 4Proposed methodology
  5. 5Competing explanations and how the design discriminates among them
  6. 6Clinical and engineering implications
  7. 7Limitations
  8. 8Conclusions

Abstract

Background. Implant failures are often described as concentrated in a small share of patients, yet published estimates of within-patient correlation span a wide range, and many implant studies still analyze implants as independent units. Three questions are conflated: how much clustering exceeds what chance produces when a rare event is spread over patients with unequal numbers of implants; what explains any excess (a stable host factor, the operator or centre, shared site or prosthetic conditions, or contagion between adjacent sites); and what ignoring clustering does to inference.

Objective/Hypothesis. We hypothesize that, once the chance baseline is removed and estimates are placed on one scale, the excess clustering of early implant failure is smaller and more uniform across cohorts than the published range suggests, and that a patient-level variance component remains separable from operator and site components.

Proposed approach. We define (i) the exact distribution of patients with two or more failures under independence; (ii) the design effect and beta-binomial overdispersion with their link to the intraclass correlation (ICC); (iii) a shared-frailty model with crossed patient, operator, and centre effects and a variance-partition rule on a defined latent scale; and (iv) a harmonized re-analysis protocol and a design that exploits patients treated at separate surgeries or by more than one operator. An illustrative Monte Carlo computation under stated assumptions (not empirical data) shows that pure chance can place about half of all failures in the top 5% of patients when per-implant risk is 3%, and that ignoring clustering inflates the nominal 5% type I error to 7% to 31% for ICC between 0.05 and 0.60.

Expected contribution. A comparable metric, a chance benchmark, and an identification strategy for host versus operator effects, with numbered predictions and refuting results.

Conclusions. Headline statements such as “a few percent of patients carry most failures” are uninterpretable without the denominator, the failure definition, and the implants-per-patient distribution. The framework is untested on real data and requires registry or multicenter data that carry operator identifiers.

1. Introduction

A person who loses one implant is more likely to lose another than a person who has lost none. This observation, first quantified in implant cohorts in the early 1990s, is usually taken to mean that some patients carry a susceptibility that is not captured by the recorded covariates [1, 2]. The practical consequences are large. If failures are correlated within patients, implants cannot be treated as independent observations in a significance test, sample-size calculation, or meta-analysis, and “patient susceptibility” becomes a target for prevention and prediction.

Three questions have been merged in the literature, each needing a different method.

The first is descriptive and arithmetic. A rare event distributed over patients with unequal numbers of implants will produce some patients with several failures even if every implant had the same, independent risk. How many such patients should be expected by chance depends on the per-implant failure probability and on the distribution of implants per patient, which varies from one implant in a single-tooth patient to eight or more in a full-arch patient. A cohort statistic such as “4.8% of patients had 57% of failures” cannot be interpreted until the chance expectation under the same definition has been computed.

The second is causal. A correlation among implants in one mouth can arise from a stable host factor (systemic, genetic, immunologic, behavioral), from the operator or centre that treated the patient, from shared local conditions (jaw, bone quality, splinted prosthesis, one implant system), or from interaction between neighboring sites in which one failure raises the hazard of the next. These sources differ in what they predict for implants placed at separate surgeries, by different operators, or at distant sites, and the usual single-level analysis cannot distinguish them.

The third is inferential. Ignoring clustering leaves point estimates broadly unchanged but understates standard errors for exposures that vary between patients, so false-positive rates rise. The size of the inflation is governed by the ICC and the cluster size, and ICC estimates are not comparable across cohorts when they are computed on different scales.

This manuscript proposes a common statistical framework for all three questions and a design that can apportion the excess between host and operator. It is a methodological and theoretical proposal. No patient data were analyzed; the only numbers we generate come from a Monte Carlo and closed-form computation with stated parameters. Evidence appraisal is at the abstract level.

2. Background and critical appraisal of the evidence

Origin and quantification of the concept

Weyant and Burt analyzed 598 patients with 2,098 implants from a Veterans Affairs registry using life tables and a correlated binomial model. They reported an implant-level 5.6-year survival of 89.9% against a patient-level survival of 78.2%, a within-patient correlation of removals of 0.11, and 1.3-fold higher odds of a second removal after a first [1]. Herrmann and colleagues examined 1,738 implants in 487 patients from four multicenter studies and concluded that dependency existed among implants in one patient or jaw, the risk to remaining implants rising after a first failure; they proposed analyzing one randomly selected implant per patient [2]. Chuang and colleagues compared three estimators in 660 patients with 2,286 implants (one random implant per patient, all implants assuming independence, all implants allowing dependence) and found that 5-year survival and its standard error varied little across models overall, whereas in smokers the standard errors differed more (8.2%, 4.0%, and 5.6%, respectively) [3]. Together these three papers establish both the phenomenon and the point that its practical weight depends on the stratum.

Chrcanovic and colleagues studied 1,406 patients with at least three implants (8,337 implants, 592 failures) and defined “cluster behavior” as three or more failures in a patient; 67 patients (4.77%) met this definition and carried 56.8% of all failures. Antidepressant intake and bruxism were associated with cluster behavior at the patient level [4]. Earlier clinical descriptions of cluster-failure patients exist [5, 6]. A recent scoping review of five studies on modern roughened surfaces (9,986 implants, 858 failures) reported that 25.2% of failures showed cluster behavior (defined as two or more failures in one patient within 2 years) and a prevalence of 2.1% [7]. These two summaries use different definitions of the same word, and neither provides a chance benchmark.

Griffin and colleagues used a mixed-effects logistic model in 132,675 US veterans with 468,496 implants (13,492 failures in 9,423 veterans) and reported an ICC of 86% for patient-level clustering [8]. This is the largest estimate in the largest cohort. Because the abstract does not state the scale, the covariates, or the way early and late failures were pooled, we cannot tell whether 0.86 is a latent-scale ICC, and we return to this in Section 3.7.

Survival-model work with frailty

Fagbamigbe and colleagues compared 13 survival regression models, including frailty models, in a Swedish cohort of 596 patients followed 9 years for implant loss, peri-implantitis, or technical complications, and found that a flexible parametric model with frailty fitted best [9]. A companion analysis in the same cohort reported that peri-implantitis and implant loss clustered with other complications in the same patient, whereas technical complications were mostly isolated events [10]. A 2026 multi-task survival model treated dependent failure and reimplantation events [11]. These studies show that frailty models are applicable to implant data. They do not report a cross-cohort comparison of ICC, a chance benchmark, or a partition that includes the operator.

Frailty, an unobserved multiplicative factor on the hazard shared by members of a cluster, originates in work on heterogeneity in survival data [12, 13]. For binary clustered data, estimators of the intraclass correlation and their properties are well characterized [14, 15], and the median odds ratio gives a scale-free description of between-cluster heterogeneity in multilevel logistic models, with a recent extension to three levels [16, 17]. The ICC from a generalized linear mixed model is defined on the latent (link) scale and differs numerically from an observed-scale correlation [18]. None of this has been applied systematically to implant cohorts.

Operator and centre effects

Jemt and colleagues analyzed 11,074 operations by 23 dentists at one clinic over 28 years, with 616 early failures (5.6%). Failure rates differed between surgeons, and the surgeons lowered their failure rates after moderately rough surfaces replaced turned surfaces, but the relationship of failure rates between surgeons was maintained [19]. The analysis used chi-square comparisons without patient-level adjustment. In a nationwide dental chain, 26,865 implants placed by 27 oral surgeons and 30 periodontists showed no significant difference in early failure by specialty (1.3% versus 1.7%), but the number of implants placed during specialty training predicted failure [20]. These findings are consistent with a real operator component, but they leave open how much of it is case-mix, because operators are not randomly assigned to patients.

Unit-of-analysis problems

Fleming and colleagues hand-searched 30 issues of each of five dental specialty journals and found that, among 559 studies with inherent clustering, 223 (39.1%) adjusted for it [21]. In a systematic review of outcome measures in implant studies, the implant was the unit of analysis in nearly all reports (98.6% according to the notes supporting this manuscript), with little consideration of clustering [22]. Only about 12% of implant randomized trials were reported to have a correct sample-size calculation [23]. Standard errors were often omitted in time-to-event dental articles [24], and split-mouth implant trials were poorly reported [25]. Faggion and colleagues showed in one worked example (sinus membrane perforation and implant failure) that a significant pooled odds ratio of 0.49 became less certain when heterogeneity, publication bias, and clustering were considered [26]. In a meta-analysis of bisphosphonate and denosumab exposure and in cohort studies of proton pump inhibitor exposure, significance has been reported to differ between implant-level and patient-level analyses [27, 28, 29]. These are scattered cases, not a measured rate of flipped conclusions.

Proposed explanations for patient-level excess

Reported correlates of cluster behavior include antidepressant use and bruxism [4], sparse trabecular architecture in the posterior mandible (a 20-case, 20-control study) [30], and promoter polymorphisms in matrix metalloproteinase genes (a systematic review of five studies) [31]. Failed-implant sites do worse when reimplanted [32, 33], and in a retrospective study no patient-level predictor was identified [33]. Bone-loss pattern is similar between implants within a patient [34], and peri-implantitis prevalence rises with implant number [35]. Immune profiling stratified patients with peri-implantitis [36], but the microbiome signature appears site-specific, not patient-wide [37]. A periodontal analogue (17 persons followed 25 years) suggests that responders to experimental gingivitis may be predisposed to periodontitis, a finding the authors describe as hypothesis-generating [38]. None of these correlates has been replicated prospectively, and none was tested while holding operator and site constant.

Summary table

Table 1. Pivotal studies, design, main bias, and operational evidence level. Levels are operational categories, not GRADE: A strong; B moderate; C preliminary; D mechanistic or theoretical; E speculative.
StudyDesign and sizeFinding relevant hereMain bias or limitLevel
Weyant 1993 [1]VA registry, 598 patients, 2,098 implantsCorrelated-binomial rho 0.11; patient survival 78.2% vs implant 89.9%Single system, observed-scale rhoB
Herrmann 1999 [2]4 multicenter studies, 487 patients, 1,738 implantsDependency among implants; analyze one implant per patientStatistical detail not in abstractC
Chuang 2001 [3]660 patients, 2,286 implantsSmall effect on survival; larger SE differences in smokersSingle cohortB
Chrcanovic 2017 [4]Retrospective, 1,406 patients with at least 3 implants4.77% of patients with 56.8% of failuresSelected on implant count; no chance baselineC
Jemt 2016 [19]One clinic, 23 surgeons, 11,074 operationsSurgeon differences persist across surfacesUnadjusted, case-mixC
Griffin 2025 [8]Registry, 132,675 patients, 468,496 implantsICC 86%Scale not visible at abstract levelC
Fagbamigbe 2021 [9]Swedish cohort, 596 patientsFrailty models fit bestOne cohort, composite outcomeC
Fleming 2013 [21]Hand-search of 5 journals39.1% of clustered studies adjustedNot implant-specificB
Faggion 2024 [26]Worked meta-analysisClustering reduced confidence in a pooled OROne exampleC

3. Hypothesis and theoretical framework

Formal statement and assumptions

Hypothesis. For early implant failure (removal within 12 months of placement) in modern cohorts, (H1) the number of patients with two or more failures exceeds the chance expectation computed from the same cohort’s implants-per-patient distribution; (H2) when all cohorts are analyzed with one estimator, one failure definition, and one follow-up window, the between-cohort spread of the latent-scale ICC is much smaller than the spread of published values; (H3) a patient-level variance component remains after adjustment for operator, centre, surgical session, and local covariates; and (H4) its share of total frailty variance is larger than the operator-plus-centre share for late failure and peri-implantitis and at least comparable for early failure.

Notation. Patient i = 1,…,N receives mi implants; Yij is 1 if implant j fails within the window. p is the marginal failure probability, q = 1 − p, m̄ the mean of mi, and CV the coefficient of variation of mi. All probabilities are per implant. Time is in months.

Assumptions. (A1) Failure is defined identically across cohorts (implant removal, not “mobility” or bone-loss thresholds). (A2) Follow-up is administratively censored and non-informative for the window analyzed. (A3) Death and loss to follow-up are rare in the window; otherwise cause-specific hazards are used. (A4) Within one cohort, a single marginal risk p applies for the chance benchmark; heterogeneity in p from measured covariates is handled by standardization (Section 4.3). (A5) Operator identifiers are recorded and persistent.

Design effect

If implants within a patient share an observed-scale correlation ρ, then Cov(Yij, Yik) = ρpq for j ≠ k, and the variance of the number of failures in a patient is

Var(Y_(i⋅))=m_i p q ( 1+(m_i−1)ρ ).

For equal cluster size the variance inflation relative to independence is the design effect

DE=1+(m−1)ρ.

With unequal sizes and a ratio estimator of the failure proportion, the inflation is

DE_w=1+((E(m^2))/(E(m))−1)ρ=1+(m (1+CV^2)−1)ρ,

which exceeds DE whenever sizes vary. The effective number of implants is n/DEw. In the simulated cohort of Section 4.5, m̄ = 3.6 and E[m²]/E[m] = 5.5, so DEw = 1 + 4.5ρ, not 1 + 2.6ρ. For a contrast between treatment arms that vary between patients, the true null variance of the naive implant-level test statistic is DEw times the variance it assumes, so the actual two-sided type I error at nominal 0.05 is approximately 2[1 − Φ(1.96/√DEw)]. For a contrast applied within patients (split-mouth), the naive test is conservative, with the variance of the difference reduced by a factor of about 1 − ρ for a balanced pair; we do not simulate this case.

Beta-binomial overdispersion and its link to ρ

Let the patient-specific failure probability πi follow a Beta(a, b) distribution and, given πi, let Yi· ~ Binomial(mi, πi). Then p = a/(a + b), and the observed-scale intraclass correlation is

ρ=1/(a+b+1),  a=p(1/ρ−1), b=q(1/ρ−1).

The probability mass is P(Yi· = k) = C(mi, k) B(k + a, mi − k + b)/B(a, b), where B is the beta function. The variance equals the expression in Section 3.2, so ρ is the overdispersion parameter; ρ → 0 recovers the binomial. The probability that a second implant fails given that a first has failed is p + ρq. For p = 0.07, this equals 0.117, 0.172, and 0.275 at ρ = 0.05, 0.11, and 0.22. This conditional probability is a risk difference of ρq, which is different from an odds ratio, so the correlation of 0.11 and the 1.3-fold odds reported in the first quantification [1] are not directly interchangeable; the harmonized protocol therefore reports both.

A moment estimator that can be computed from a published table of failures per patient is

ρ=(P_2−p^2)/(p (1−p)),  P_2=(∑_i^​ y_i(y_i−1))/(∑_i^​ m_i(m_i−1)),

where yi is the number of failures in patient i and p̂ = Σyi/Σmi. Likelihood-based and moment estimators for binary clustered data differ in bias and efficiency [14], and confidence intervals need care when events are rare [15].

Chance expectation of “patients with two or more failures”

Under independence, a patient with m implants has P(Y ≥ 2 | m) = 1 − qm − m p qm−1. If wm is the share of patients with m implants, the expected proportion of patients with at least two failures is Σm wm P(Y ≥ 2 | m), and the expected share of all failures contained in such patients is Σm wm Σk≥2 k P(Y = k | m) / (p m̄). A threshold c replaces 2 for definitions such as “three or more failures”. A conditional exact test keeps each mi and the total number of failures F fixed and distributes failures at random over the M = Σmi implants; then the expected number of within-patient failure pairs is F(F − 1) Σmi(mi − 1) / [M(M − 1)], and the observed count is referred to the resampled distribution. This removes the dependence on any assumed p. A related but distinct statement, “the top 5% of patients carry X% of failures”, has an additional dependence: when only about 10% of patients have any failure, the top 5% by failure count will carry roughly half of failures even under independence (Section 4.5).

Latent-scale ICC and the median ratio

For a random-intercept logistic model, logit P(Yij = 1 | ui) = β0 + x′β + ui, with ui ~ N(0, σ²P), the latent-scale intraclass correlation is

ρ_L=(σ_P^2)/(σ_P^2+π^2/3),

and the median odds ratio between two randomly chosen patients with identical covariates is MOR = exp(√(2σ²P) × 0.6745) [16]. The constant 0.6745 is the 75th percentile of the standard normal. The three-level extension adds operator and centre terms [17]. The relation between ρL and the observed-scale ρ depends on p: for a baseline logit of −2.944 (about 5%), our computation gave observed-scale ρ of 0.014, 0.032, 0.075, 0.168, and 0.312 for σ²P of 0.25, 0.5, 1, 2, and 4, corresponding to ρL of 0.071, 0.132, 0.233, 0.378, and 0.549. The same latent variance therefore gives a much smaller observed-scale correlation when the event is rare. This scale dependence is the central obstacle to comparing published ICCs [18].

Shared-frailty model with crossed patient, operator, and centre effects

For implant j of patient i, placed in surgical session g by operator s in centre c, we propose the hazard

λ_(ij)(t)=λ_0(t) exp​(x_(ij)′β+u_i+v_s+w_c+z_(ig)+γ f_(ij)(t)),

with ui ~ N(0, σ²P) for the patient, vs ~ N(0, σ²S) for the operator, wc ~ N(0, σ²C) for the centre, and zig ~ N(0, σ²G) for the surgical session within a patient. Operators are crossed with patients when some patients are treated by more than one operator, and nested within centres when each operator works in one centre. The term fij(t) is a time-varying covariate encoding prior failure of other implants in the same patient, weighted by inter-implant distance, and γ is its coefficient (contagion). Gamma frailty with variance θ is an alternative, with Kendall’s τ = θ/(θ + 2) as pairwise concordance [12, 13].

Variance partition. For continuous-time frailty there is no residual variance, so the share of “total variance” is undefined. We therefore report two quantities. The first is the relative partition of frailty variance, sP = σ²P / (σ²P + σ²S + σ²C + σ²G), and analogously for each component; it is invariant to the choice of residual. The second is an absolute ICC obtained by fitting the same structure as a discrete-time complementary log-log model on yearly or monthly intervals, for which the residual variance is π²/6, so that ICCP = σ²P / (σ²P + σ²S + σ²C + σ²G + π²/6). Component-wise median hazard ratios, MHR = exp(0.6745√(2σ²)), allow each source to be expressed as a ratio.

Identification. In a design where each patient is treated by one operator, σ²S is estimated from differences between operators’ caseloads and is therefore confounded with unmeasured host differences between those caseloads. The patient component σ²P is estimated within operators from implants in the same patient, but implants placed in the same session also share the session and local conditions, so σ²P and σ²G are not separable without implants from different sessions. When some patients have sessions with different operators, σ²S can be estimated from within-patient contrasts, which hold the host fixed. Estimability requires a connected patient–operator graph: the bipartite graph linking patients to operators must have one large connected component; isolated operator–patient pairs contribute nothing to separating the two components.

Reading the published range on a common scale

Two quantities in the 0.11 to 0.86 range are not on the same footing. The first, 0.11 [1], is an observed-scale correlation from a correlated binomial model. The second, 0.86 [8], was calculated from a mixed-effects logistic model. If 0.86 were a latent-scale value, then σ²P = 0.86 × (π²/3)/(1 − 0.86) = 20.2 and the MOR would be about 73, meaning that the median ratio of odds between two randomly chosen veterans would be 73-fold. The abstract’s counts suggest a more modest observed pattern: 13,492 failures in 468,496 implants (2.9%), 9,423 affected patients among 132,675 (7.1%), and 1.43 failures per affected patient. A back-of-envelope computation under independence, using the same implant count per patient (3.53 on average, assumed fixed or geometric), gives 9.5% to 9.8% of patients affected and 1.04 to 1.07 failures per affected patient. The observed values indicate clustering, but the share of affected patients is lower than independence implies, which might reflect censoring, differing follow-up, or a mismatch between the modeled and counted cohorts. We cannot resolve this at abstract level; the point is that a headline ICC cannot be compared across cohorts without the model, scale, and denominator.

Numbered predictions and refuting results

P1 (chance baseline). In each published or accessible cohort that reports failures per patient, the observed number of patients with at least two failures exceeds the conditional-exact expectation (one-sided P < 0.05) in most cohorts. Refuted if the observed count lies within the 95% resampling band in half or more of cohorts with at least 100 failures.

P2 (harmonization). The spread (maximum minus minimum) of cohort-specific latent-scale ICCs for early failure, estimated with one model and one window, is less than 0.2 and smaller than the spread of the originally published values. Refuted if the harmonized spread is 0.2 or more with confidence intervals that do not overlap across the extreme cohorts.

P3 (host component). The patient variance σ²P has a lower 95% profile bound above zero after adjustment for operator, centre, session, jaw, splinting, and implant system. Refuted if the bound includes zero in cohorts with adequate precision (relative SE of σ²P below 0.35).

P4 (partition). For early failure, sP exceeds the operator-plus-centre share, and the excess is larger for late failure and peri-implantitis. Refuted if operator-plus-centre share exceeds sP for early failure in two or more independent cohorts.

P5 (separate surgeries). The correlation between failures of implants placed at different surgical sessions in one patient is at least half the correlation within one session. Refuted if the between-session correlation cannot be distinguished from zero while the within-session correlation is positive, which would implicate session-level and local causes over a stable host factor.

P6 (contagion). After frailty adjustment, γ is close to zero and the hazard is not graded by distance to the failed implant. Refuted if hazard declines monotonically with distance, with γ clearly nonzero.

P7 (inference). For exposures that vary between patients, the ratio of cluster-robust to naive standard errors is approximately √DEw computed from the cohort’s ρ and size distribution (within 20%). Refuted if the ratio departs from this by more than 20% in most cohorts.

4. Proposed methodology

Design overview

The proposal has four components, shown in Figure 1 and Figure 2: a chance benchmark for cluster statistics; a harmonized re-analysis of existing cohorts; a crossed-effects analysis that partitions variance among patient, operator, centre, and session; and a staged-surgery or multi-operator subset that identifies host and operator effects through within-patient contrasts. The first two components need only failures and implants per patient; the last two need operator identifiers and surgery dates.

Data sources and eligibility

Eligible data are implant-level records with patient identifier, implant position, placement date, surgical session, operator code, centre code, implant system, loading protocol, failure date and reason, and censoring date. Candidate sources are registries, university clinics, dental chains, and multicenter trial datasets of the type that have already supported clustering or operator analyses [4, 8, 19, 20]. We have not contacted any data holder, and data availability is the largest practical uncertainty. Where patient-level data cannot be moved, a federated scheme is proposed: each site runs a shared script and returns only variance-component estimates, their covariance, and aggregate failure-per-patient tables, which can be pooled by random-effects meta-analysis on the latent scale.

Harmonized re-analysis protocol

All cohorts are analyzed with the same estimator, outcome, window, and covariate set, fixed in a registered analysis plan before any data are opened.

  • Outcome. Implant removal for any reason (primary). Secondary outcomes are removal within 12 months and removal within 5 years, with death and loss to follow-up as competing or censoring events. A negative-control outcome (technical prosthetic complication, which is not expected to depend on osseointegration) is analyzed with the same models.
  • Eligible implants. Implants placed in a common calendar window with at least the window’s follow-up available or an event. First-placement implants form the primary set; implants at previously failed sites are analyzed separately because survival there is lower [32, 33].
  • Estimators. (a) The moment estimator ρ̂ of Section 3.3 from failures-per-patient tables; (b) a beta-binomial maximum-likelihood fit; (c) a random-intercept logistic model reporting ρL and MOR; (d) a crossed discrete-time complementary log-log model with patient, operator, centre, and session effects reporting sP, ICCP, and component MHRs; (e) a continuous-time shared-frailty Cox model as a robustness check; (f) a generalized estimating equation with exchangeable working correlation and robust variance, and a one-random-implant-per-patient estimate with 1,000 resamples [2, 3].
  • Standardization. Because p varies between cohorts, ICC is reported both unadjusted and after adjustment for a fixed set of covariates (age band, sex, smoking, jaw, arch, splinting, implant system, surface class, bone augmentation).
  • Reporting. For each cohort: N, implant count, distribution of mi (mean, CV, maximum), p, failures per patient, P2 and its conditional-exact reference, ρ̂, ρL with confidence interval, MOR, and, where operator codes exist, the variance partition.

Design for separating host from operator

Four sources of within-patient variation in operator or session are available.

Staged surgeries. Patients who received implants in separate sessions, months or years apart, provide implants that share the host but not the session. The between-session correlation (P5) isolates host-level correlation from session-level and local causes.

Operator switching. In teaching clinics, group practices, and referral networks, the same patient is often treated by different operators at different sessions, so the patient–operator graph is connected and σ²S is estimated from within-patient contrasts. A connectivity criterion is applied: the largest connected component must contain at least 80% of implants and at least 10 operators, each linked to at least 5 patients with two or more operators, before the crossed model is interpreted. These thresholds are unvalidated proposals.

Reimplantation. A failed site reimplanted in the same patient, often by a different operator, is a natural contrast, but the outcome is conditioned on a prior failure and is subject to site-level confounding [32, 33].

Prospective operator allocation. Within a single teaching clinic, the operator for each session could be assigned by a documented rota or randomization among operators of equivalent credentials, with patients consenting to either. This is the only design that breaks case-mix confounding by construction. It requires ethical approval and was not performed.

Precision for the operator component. For a balanced random-effects design with J operators, the relative standard error of a variance component is approximately √(2/(J − 1)): 0.47 for 10 operators, 0.32 for 20, and 0.23 for 40. These values describe the operator component under a simplified balanced design; the unbalanced crossed model needs a simulation-based power analysis that we have not done. A single large clinic may offer J near 23 [19].

Sample size for a between-patient comparison. For two arms with failure proportions p1 = 0.05 and p2 = 0.025, two-sided α = 0.05, and power 0.80, the independent-implant requirement is 905 implants per arm. Using DE with m̄ = 3.5, the requirement becomes 1,019 implants (291 patients) per arm at ρ = 0.05, 1,154 (330 patients) at ρ = 0.11, and 1,584 (453 patients) at ρ = 0.30 (computed with the script in the paper folder). Planning with ρ between 0.05 and 0.30 therefore changes the required patients by a factor of about 1.6, and guidance for cluster trials addresses uncertain ICC [39].

Illustrative computation under stated assumptions — not empirical data

We ran a Monte Carlo and closed-form computation (script sim38.py, output sim38_output.txt; random seed 38) to show two effects.

Assumptions. Implants per patient m takes the values 1, 2, 3, 4, 6, 8, and 10 with probabilities 0.25, 0.20, 0.15, 0.15, 0.10, 0.10, and 0.05, giving m̄ = 3.6 and E[m²]/E[m] = 5.5 (hypothetical). Per-implant failure probability p is 0.03, 0.05, or 0.08. Within-patient dependence is beta-binomial with ρ ∈ {0, 0.05, 0.11, 0.2, 0.4}. Part (a) uses 200,000 patients per scenario. Part (b) compares two arms of 200 patients each (randomized by patient), with p = 0.06, no true treatment difference, and 4,000 replicates per ρ; Monte Carlo standard error near 0.05 is about 0.0034. The naive test is a two-proportion z-test on implants; the robust test uses a patient-level cluster-robust variance of the ratio estimator with a t reference; the third test draws one implant per patient.

Table 2. Illustrative computation: apparent concentration of failures by chance and under clustering (200,000 simulated patients per row; hypothetical implants-per-patient distribution).
Failure risk pρTop 5% of patients: share of all failures (%)Patients with at least 2 failures (%)Share of failures in those patients (%)
0.03052.50.6512.5
0.030.1168.21.6937.4
0.030.4091.22.3867.0
0.05038.21.7420.2
0.050.1152.73.1342.2
0.050.4073.94.0968.9
0.08032.83.8428.7
0.080.1143.55.5347.2
0.080.4059.56.5270.0

Under independence, the closed-form expectation of patients with at least two failures was 0.66%, 1.70%, and 3.93% at p = 0.03, 0.05, and 0.08, and the corresponding shares of failures were 12.5%, 19.8%, and 29.3%, in agreement with the Monte Carlo rows.

Two results matter for interpretation. First, “the top 5% of patients carry about half of failures” arises by chance at p = 0.03 (52.5%), because only about 10% of patients have any failure and every failing patient ranks above the rest; this statistic cannot be interpreted without the proportion of patients with any failure. Second, the more specific definition of cluster behavior is far from chance in the Chrcanovic cohort [4]. Taking every patient to have six implants (observed mean 8,337/1,406 = 5.93) and p = 592/8,337 = 0.071, independence implies 0.61% of patients with three or more failures, against 4.77% observed (7.8-fold), and 4.4% of failures in such patients, against 56.8% observed. A beta-binomial model matched to the observed 4.77% needs ρ = 0.22 and would put 40% of failures in those patients; the larger observed share (56.8%) suggests either a heavier-tailed distribution of patient risk than a single beta distribution (for instance a small high-risk subpopulation) or that the assumption of six implants for everyone is too crude.

Table 3. Illustrative computation: type I error at nominal 0.05 for a null between-patient treatment comparison (200 patients per arm, p = 0.06, 4,000 replicates; hypothetical size distribution).
ρDEw = 1 + 4.5ρAnalytic naive rejectionSimulated naive implant-level testCluster-robust (patient)One implant per patient
01.000.0500.0550.0540.051
0.051.230.0770.0730.0460.048
0.111.500.1090.1000.0470.048
0.201.900.1550.1530.0540.050
0.402.800.2410.2430.0490.050
0.603.700.3080.3050.0510.049

The simulated variance of the arm difference exceeded the independence variance by factors of 1.04, 1.20, 1.46, 1.90, 2.78, and 3.69 across the same ρ values, close to DEw. The naive rejection rate rises to about twice nominal at ρ ≈ 0.11 and exceeds six times nominal at ρ = 0.6. The one-implant-per-patient analysis is valid but discards information, in line with the recommendation of Herrmann and colleagues [2]. The computation does not address within-patient (split-mouth) contrasts, time-to-event analysis, or informative censoring.

Statistical analysis plan

Variance components are tested by likelihood-ratio tests with a 50:50 mixture of χ² reference distribution for boundary parameters, and reported with profile-likelihood intervals. For crossed models with few operators, a Bayesian fit with weakly informative half-normal priors on standard deviations is run as a sensitivity analysis. Between-cohort heterogeneity of ρL is summarized by τ² on the logit-transformed scale and by leave-one-cohort-out analysis. To handle non-random operator allocation, operator effects are estimated both with and without patient-level adjustment and, in the switching subset, with patient fixed effects. P1 to P7 are pre-specified; secondary outcomes are labeled exploratory.

Ethics and feasibility

Retrospective analysis of de-identified registry data may need approval or a waiver from the data holder’s board. Operator identifiers raise reporting risk; operator codes should be randomized, operator-level estimates should not be published, and only variance components reported. Prospective operator allocation requires full ethical review and informed consent. No approval, registration, or funding exists for this proposal.

5. Competing explanations and how the design discriminates among them

Chance. The conditional-exact test (P1) is designed to isolate it. A cohort whose failures per patient follow the null distribution shows no excess clustering, whatever its headline concentration statistic.

Scale artefact. If published ICCs differ only because of scale, definition, follow-up, or implants per patient, harmonization (P2) shrinks the spread. If the spread persists, the differences are genuine heterogeneity between populations, systems, or protocols.

Operator or centre. The crossed model with within-patient switching separates operator variance from host variance. If clustering were mainly operator-driven, σ²P would fall toward zero when operator and session are included (P3 refuted), and a patient moved to a different operator would lose their excess risk.

Shared local conditions. Jaw, bone quality, splinting, and implant system are covariates and stratifiers. Residual local clustering is detected by the session effect σ²G: if σ²G is large and the between-session correlation (P5) is near zero, the correlation is local or procedural, not a stable host trait. Distance-graded dependence points the same way.

Contagion. A failure that raises the hazard of neighbors through infection, overload redistribution, or surgical re-intervention predicts a positive, distance-graded γ and a time pattern in which the hazard jump follows the failure date. Pure frailty predicts that implants in distant sites of the same patient are as correlated as adjacent ones and that the hazard of survivors rises after the first failure only through selection for high-frailty patients. The two are not fully separable by timing alone, which is why graded distance and separate sessions are both used.

Stable host factor. The host-factor account predicts persistence of correlation across sessions and operators (P3, P5) and a measurable role for candidate markers. Candidate markers such as medication use and bruxism [4], trabecular architecture [30], or polymorphisms [31] can be tested by adding them to the model and examining how much σ²P shrinks.

Mechanism limits. A variance share is descriptive. A large σ²P is compatible with several biologies, and a small σ²P is compatible with a strong effect of a rare trait. The framework tells where to look; it does not identify the mechanism.

6. Clinical and engineering implications

These implications are conditional on the predictions holding in real data.

Reporting. If P1 and P2 hold, implant studies could report, beside survival, the distribution of failures per patient, m̄ and CV, the observed-scale ρ̂ and the latent-scale ρL with interval. The same table would allow later meta-analysts to impute ρ for studies that omit it.

Trial design. Between-patient comparisons would be planned with DEw from a ρ range appropriate to the outcome, and the analysis would use patient-level or cluster-robust methods; one random implant per patient is a valid but inefficient fallback [2, 3]. Because ρ is uncertain across cohorts, sample-size plans should show sensitivity over a range, as in Section 4.4 and as cluster-trial methodology advises [39].

Risk management. If a stable patient-level component dominates (P3, P4), a first failure would warrant closer review of remaining implants, consistent with the dependence reported earlier [2]. If operator or session components dominate, the response would target technique, training, and protocol, as the association of training-period case numbers with early failure suggests [20]. If contagion dominates, the response would concern local infection control and load distribution. None of these actions has been tested.

Engineering. Implant system, surface, and prosthesis design enter as covariates. A 20-year prospective report found four of seven failures in one patient [40], so device performance in small samples can hinge on a single patient and should be reported with a patient-level interval.

7. Limitations

  • No data. Every quantitative statement about the literature is taken from abstracts or from the notes that supported this manuscript. The computations in Section 4.5 depend on assumed distributions that may not resemble real cohorts. They show what chance and ignoring clustering can do, not what is happening in any cohort.
  • Beta-binomial is a model. Real patient risk may be a mixture with a small high-risk subpopulation, which the beta distribution describes poorly; the Chrcanovic arithmetic in Section 4.5 hints at this. Tail behavior affects both the chance benchmark and the identification of cluster patients.
  • Crude size assumptions. The Chrcanovic and Griffin back-calculations assume fixed or geometric implants per patient; the real distribution of mi should replace them.
  • Scale definitions. The latent-scale ICC depends on the link and the residual-variance convention, and the observed-scale ρ depends on p. Harmonization removes arbitrary differences but cannot stabilize a rare-event ICC; intervals will be wide.
  • Confounded operator effects. Observational operator effects mix skill with case allocation, referral patterns, and protocol. Only the switching subset or prospective allocation separates them, and those designs may not be available.
  • Selection into the switching subset. Patients treated by several operators or in separate sessions are atypical (complex or multi-stage plans), and selection could itself relate to failure risk.
  • Failure definition and time. Early failure, late failure, peri-implantitis, and non-biological removal are different processes; pooling them can create or mask clustering. Precautionary removal of a failing patient’s remaining implants is informative censoring that creates dependence by clinical decision.
  • Selection on implant count. Analyses restricted to patients with at least three implants [4] condition on a variable related to anatomy and treatment plan, and thus to risk.
  • Meta-research effect not estimated. How often a cluster-appropriate analysis changes the conclusion of an implant trial or meta-analysis is not measured here. Case reports of such changes exist [26, 27, 28, 29], but a frequency requires a systematic audit.

8. Conclusions

Within-patient clustering of implant failure is an established phenomenon, but its magnitude is reported on incompatible scales, and its common summaries, such as the share of failures in a few patients, partly reflect arithmetic of rare events and unequal implants per patient. A chance benchmark, a harmonized latent-scale ICC, and a crossed patient–operator–session frailty model address these problems in one framework. The illustrative computation shows that ignoring clustering can raise a nominal 5% error rate to 7% to 31% at ρ between 0.05 and 0.60, and that a patient-level analysis or cluster-robust variance restores the nominal rate under the stated assumptions. Whether a stable host factor survives adjustment for operator and session is an empirical question that this manuscript turns into testable predictions but does not answer.

Cite this paper

Jain S, Gupta A. Why Do Implant Failures Cluster in Patients? A Frailty-Model Framework to Separate Host, Operator, and Chance. Working paper. Center for Implant Dentistry; 2026. Available from: https://bayareaimplantdentistry.com/clinician-research-and-publications/implant-failure-clustering-frailty

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