Accuracy of automated cephalometric landmark detection with artificial intelligence: a systematic review

INTRODUCTION

Cephalometric analysis is a cornerstone of orthodontic and orthognathic diagnosis, and its first step, the identification of anatomical landmarks on a lateral or posteroanterior cephalogram, is the most tedious and error-prone part of the workflow. Manual landmarking requires a trained operator to locate each point, and the time and inter-examiner variability it introduces are well documented. The measurements that follow, the angles and distances of the skeletal classification, are only as reliable as the points on which they are anchored, so an error in a single landmark propagates into the diagnosis. Artificial intelligence, and deep learning in particular, has been proposed to automate this step, and the number of primary studies has grown rapidly since 2018.(1,2)

The clinical stakes of this step are higher than they might appear. Cephalometric measurements are used to decide whether a patient needs orthodontic treatment, whether surgery is indicated, and how the treatment should be planned, and a misclassified skeletal pattern can change all three. The manual workflow is therefore not only slow but also a source of diagnostic risk, and the prospect of replacing it with a reproducible automatic procedure is the main motivation behind the large body of work reviewed here.

The appeal of automation is concrete. Landmark identification is repeated on every patient, the task is well defined, and large annotated datasets now exist, which makes it an ideal target for supervised learning. If a model can locate landmarks with an error no larger than the variability between two human examiners, it can remove a bottleneck and standardize the analysis across clinicians.(3)

The task has a further advantage as a benchmark. A public dataset released for a landmark detection challenge in 2015, containing several hundred lateral cephalograms with 19 annotated landmarks, has become the de facto standard on which most models are compared, and it provides a common yardstick that is unusual in dental artificial intelligence.(2) The landmark set is also standardized by clinical convention, with well-established definitions for the sella, nasion, and the other points that anchor the common cephalometric measurements. These properties make cephalometric landmark detection one of the most measurable and comparable tasks in dental imaging, which is why it has attracted so many primary studies and why a focused synthesis is feasible.

At the same time, the comparability is only partial. The public benchmark uses a fixed set of 19 landmarks, whereas clinical tracing uses a larger and variable set, and many studies evaluated on private datasets with landmarks of their own choosing. The number of landmarks, and specifically the inclusion of the difficult mandibular points, therefore differs across studies, and this difference, more than any algorithmic detail, drives the spread in the reported summary statistics. This distinction between a common benchmark and a heterogeneous clinical task is central to interpreting the results that follow.

Three questions summarize what a clinician needs to know about this technology. First, what mean radial error do the models achieve, that is, how far from the manual reference does the automatic point fall on average. Second, what success detection rate do they achieve at the clinically meaningful thresholds of 2, 3, and 4 mm. Third, which architectures, datasets, and reference standards explain the differences among studies. These three questions organize the present review, and each is answered in the corresponding subsection of the results and the discussion.

The aim of this systematic review was to synthesize the accuracy, expressed as mean radial error and success detection rate, of artificial intelligence models for automated cephalometric landmark identification. The review deliberately separates the distance error from the threshold-based detection rate, because these two measures convey different information about whether a model is fit for clinical use.

METHODS

RESULTS

Study selection

The searches retrieved 225 records, of which 49 duplicates were removed and 176 unique records were screened (Figure 1). Title and abstract screening excluded 109 records, leaving 67 reports assessed for eligibility. Of these, 24 were excluded: 11 because no quantitative accuracy metric was reported, 10 because the outcome was not landmark detection, and the remainder for a retracted report, a duplicate, a non-cephalogram modality, or an unverifiable reference. Forty-three studies were included (43).

DISCUSSION

The answer to the first question, the mean radial error, is that artificial intelligence models locate cephalometric landmarks within roughly 1 to 2 mm of a manual reference in most studies. This is within the range of inter-examiner variability reported for manual landmarking and is therefore clinically encouraging.(3) The answer to the second question, the success detection rate at 2 mm, is that performance is heterogeneous, from below 30% to above 95%, and depends strongly on which landmarks are included and which dataset is used. The answer to the third question is that the architecture matters less than the dataset and the landmark set, because convolutional networks, transformers, and even hand-crafted-feature models converge to similar accuracy when evaluated on the same benchmark.(6,18,20)

The first answer deserves a qualification. A mean radial error near 1 mm is encouraging only if the error is uniform, and the per-landmark reports show that it is not. The gonion and condylion, which anchor the mandibular plane and the ramus measurements, are the points that matter most for skeletal classification and are also the points that the models locate least reliably.(26,38) A clinician who relies on an automatic gonion that is occasionally off by several millimeters will propagate that error into the mandibular plane angle and, from there, into the skeletal diagnosis. The mean radial error therefore understates the clinical risk for the very measurements that orthodontists weigh most heavily.

These findings align with and refine the earlier syntheses. A review of artificial intelligence in orthodontic diagnosis reported that landmark detection was among the most mature applications, with high accuracy but limited clinical translation.(1) A comprehensive review of cephalometric analysis with artificial intelligence reached the same conclusion.(2) A narrative review of artificial intelligence in cephalometric analysis emphasized the promise while noting the absence of external validation.(3) A recent systematic review with meta-analysis of the SNA, SNB, ANB, and WITS measures concluded that automatic detection is reliable for these derived measurements.(49) The present review adds the observation that the summary statistics conceal a wide spread at the 2 mm threshold, which is the threshold that determines whether a landmark is usable for a measurement.

The apparent contradiction between the favorable meta-analytic conclusion for the derived measurements(49) and the wide spread observed here is resolved by noting what each measures. The SNA, SNB, ANB, and WITS measures are anchored on landmarks that the models locate reliably, whereas the difficult gonion and condylion do not enter those measures and therefore do not drag down their pooled accuracy. This means that a model can be entirely adequate for the specific measurements that a meta-analysis pools while still failing on the landmarks needed for a full skeletal analysis. The two conclusions are both correct, and they are reconciled by the same per-landmark perspective that organizes this review.

For the reader who must decide whether to adopt a tool, the practical summary is as follows. The mean radial error is acceptable in most studies, the success detection rate at 2 mm is good but not uniformly high, and the weakest points are the gonion and condylion, which are also the points that anchor the skeletal classification. A tool can therefore be adopted with confidence for a reviewed first pass, but its output should be checked point by point, with particular attention to the mandibular landmarks, and it should be validated in the local patient population before it is trusted for unattended measurement.

The clinical consequence of this spread is that a mean radial error below 2 mm does not guarantee that every landmark is usable. A model with a mean radial error of 1.5 mm may still place the gonion 8 mm away, and the angular and linear measurements that depend on that point will then be wrong.(26,38) Clinicians adopting these tools should therefore verify the landmarks that anchor the measurements they actually use, rather than relying on a summary error. The commercial tools showed the same behavior, with population-dependent accuracy and weaker performance in patients with craniofacial anomalies.(23,24)

The workflow that follows from these findings is a reviewed first pass rather than an unattended replacement. The model places the landmarks, and the clinician then inspects and corrects the few that are misplaced, which converts a fully manual task into a mostly automatic one. This use preserves the time savings while keeping the clinician accountable for the measurements that drive the treatment plan. Several of the included studies explicitly framed their models in this way, comparing the time required for manual tracing with the time required to review and correct automatic output, and reported meaningful reductions.(25,32) The question for adoption is therefore not whether the model is perfect, but whether the combined error of the model and the reviewing clinician is acceptable relative to manual tracing alone.

The economics of this workflow are favorable even when the model error is not zero. If the model places most landmarks correctly, the clinician corrects only a minority, and the time saved scales with the proportion correctly placed. The success detection rate at 2 mm is therefore a direct proxy for the time saving, because a landmark within 2 mm of the reference is typically accepted without correction, whereas one outside it must be moved. This interpretation reframes the heterogeneous success detection rates: a model at 90% saves more time than one at 60%, but both save time relative to fully manual tracing, so even the weaker models may be worth deploying as a first pass provided the clinician reviews the output.

The generalizability question remains the main unresolved issue. Most models were trained and evaluated on images from a limited set of institutions and populations, and the one study that tested a commercial tool across two populations of different ethnicity reported a measurable drop in accuracy.(23) Cephalometric morphology differs across ancestry and across patients with craniofacial anomalies, and a model trained predominantly on one population cannot be assumed to transfer to another. Until prospective, multi-population validation becomes the norm, the safe assumption is that a tool performs best on the population that resembles its training data, and that local validation is a prerequisite for clinical use.

The same caution applies to image acquisition. Cephalograms are acquired on equipment from different manufacturers and with different protocols, and the contrast and geometry of the image affect the visibility of the landmarks. A model trained on one device may transfer imperfectly to another, and the included studies rarely addressed this, because most used a single acquisition source. This is a further reason to interpret the benchmark-based estimates as an upper bound, and to expect that performance in a new clinic, with a new device and a new patient population, will be somewhat lower than the published figures until a local evaluation is performed.

A further concern specific to this literature is the heavy use of the public ISBI 2015 benchmark. When many studies evaluate on the same dataset, the risk of indirect test-set leakage increases, because researchers may tune architectures and hyperparameters against the benchmark over successive publications. The result is that benchmark-based estimates may overstate performance on unseen clinical images, and the private-dataset studies, which reported a wider range of success detection rates, are likely closer to real-world performance.(10,33) Future studies should report performance on both the benchmark and an independent clinical cohort so that the gap between the two can be quantified.

The same argument extends to the private datasets, which are also reused across publications from the same groups. When a research group publishes successive models on the same institutional dataset, the later models benefit from the group's accumulated knowledge of that dataset, and the reported improvement over the earlier models may not generalize. This is a normal limitation of a young field, but it means that the absolute performance figures, more than the relative improvements, are what a clinician should weigh, and that independent reproduction remains the strongest form of evidence available.

The strengths of this review are the systematic search across three bibliographic databases, the explicit 2018 to 2025 window, the separation of mean radial error from success detection rate, and the recording of values as reported without recalculation. The limitations mirror those of the primary studies. Full text was available for only a subset of reports, so some data were extracted from abstracts. Screening and extraction were performed by a single author with artificial intelligence assistance rather than two independent reviewers, which raises the risk of selection error and warrants a dual-reviewer design in future updates. A meta-analysis was not possible given the heterogeneous landmarks, datasets, and metrics, and a pooled estimate would be misleading because the underlying landmark sets differ. Publication bias may also inflate the observed accuracy, because studies with unfavorable results are less likely to be published, and the heavy use of the same public benchmark raises the risk of test-set leakage across studies. Finally, the review could not assess the time efficiency of the tools, which is the other half of their clinical value, because the studies reported it inconsistently.

For clinical practice, the findings support using automatic landmarking as a time-saving first pass that a clinician then reviews and corrects, rather than as an unattended replacement for manual tracing. For research, the most informative next studies would validate models prospectively on external clinical cohorts, report success detection rate at 2, 3, and 4 mm by landmark, and state the inter-examiner variability of the reference so that model error can be compared against it. The broader adoption of artificial intelligence in orthodontics depends on evidence of this kind.(50)

For reporting, the field would benefit from a shared convention. At a minimum, studies should state the number and names of landmarks, the dataset and its provenance, the reference standard and its inter-examiner variability, the mean radial error and its standard deviation, and the success detection rate at 2, 3, and 4 mm by landmark. This would make studies directly comparable and would allow a future meta-analysis at the level of individual landmarks, which is where the clinical decisions actually reside. Until such reporting converges, readers should interpret any single summary figure with the caveat that it averages over landmarks of very different difficulty.

The research agenda that follows has three priorities. First, prospective validation across multiple institutions and populations, so that the generalizability question can be answered rather than assumed. Second, per-landmark reporting with the full threshold curve, so that the difficult points and the easy points can be distinguished. Third, head-to-head evaluation of the commercial tools against research models on a common external dataset, so that clinicians can choose among products on evidence rather than on marketing. These three steps would move the field from a large but heterogeneous literature of demonstrations toward a body of evidence on which routine clinical adoption can be justified.

Taken together, the evidence supports a measured conclusion. Automatic cephalometric landmark detection is mature enough to serve as a reviewed first pass, and it is not yet reliable enough, on the landmarks that anchor the skeletal classification, to be used without supervision. The distance between these two statements is small in engineering terms but large in clinical terms, and closing it requires exactly the kind of external, per-landmark validation that is currently the exception rather than the rule. For the clinician, the actionable message is to adopt the technology as an assistant, to verify the mandibular landmarks in particular, and to validate the tool in the local population before relying on its measurements. The evidence reviewed here supports that adoption while setting a clear expectation about where the residual risk lies. The field has reached the point where the remaining uncertainty is no longer about whether the technology works, but about whether it works for the specific patient, on the specific image, and on the specific landmark in front of the clinician. That is a question of validation, not of architecture, and it is the question that the next generation of studies should answer.

CONCLUSIONS

Artificial intelligence detects cephalometric landmarks with a mean radial error of roughly 1 to 2 mm in most studies, which is comparable to the variability between human examiners. The success detection rate at the 2 mm threshold is heterogeneous, ranging from below 30% to above 95%, and depends on the landmark set and the dataset more than on the architecture. The gonion and condylion are the least reliably located points and are also the ones that anchor the skeletal classification, so a summary error conceals the clinical risk for the measurements that matter most. The reference standard was manual annotation in nearly all studies, and risk of bias was moderate to high, chiefly because of benchmark-based evaluation and scarce external validation. Automatic landmarking should therefore be used as a reviewed first pass, and prospective external validation with per-landmark success detection rates is required before unattended use can be recommended.

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