Radiomics or deep learning for MRI trial biomarkers

That distinction is where the comparison between radiomics and deep learning becomes difficult.

Reported neuroimaging studies show a wide performance gap on paper. Classical radiomics with methods such as Support Vector Machines and Random Forests has produced classification accuracies from 61% to 89%. Deep learning models have reached accuracy as high as 98.2% in brain MRI applications. Those figures are technically relevant. They are not interchangeable. A model trained on harmonized, single-site data can yield a strong internal score while degrading sharply on another scanner, protocol, or patient population.

The real question is not which method produces the higher number. It is which representation remains measurable, interpretable, and clinically useful when the MRI system stops behaving like the training dataset.

The first layer: what each method extracts from MRI

Radiomics and deep learning begin with the same physical object: complex-valued MR signal sampled through k-space, reconstructed into images, and usually reduced to a region of interest. After that, their assumptions diverge.

Traditional radiomics applies an explicit feature map. The image is segmented or otherwise constrained to a target region. The algorithm calculates predefined properties such as intensity distributions, shape descriptors, local texture, gray-level co-occurrence relationships, run-length statistics, or filtered responses. These handcrafted radiomics features form a high-dimensional quantitative representation of the lesion, tissue compartment, or anatomical structure.

The feature definitions are visible. Their biological meaning is not automatically guaranteed, but the mathematical operation can be inspected. A texture feature can be traced to voxel relationships. A shape feature can be examined against the segmentation boundary. An intensity statistic can be tested for sensitivity to bias field, coil profile, receive gain, or normalization.

The classifier then operates on this engineered feature space. SVMs and Random Forests are common because they tolerate a relatively small number of subjects compared with the dimensionality of the extracted data. That tolerance is conditional. Feature selection, nested validation, leakage control, and regularization remain necessary. A radiomics matrix can overfit long before the final classifier appears unstable.

Deep learning removes much of the manual feature design. A convolutional neural network or related architecture receives image data, image patches, volumes, or multimodal sequences and learns internal representations through successive nonlinear transformations. The network can encode spatial context, cross-sequence relationships, local intensity patterns, and structures that were not specified in advance by the investigator.

This flexibility is the source of its performance advantage and its audit burden. The learned representation is not a single texture descriptor or a named geometric measure. It is distributed across many parameters. The network can yield a useful imaging biomarker without offering a direct explanation of which measurable tissue property drove the output.

The distinction is therefore not simply handcrafted features versus automatic features. It is controlled dimensionality versus adaptive representation learning.

Neither column describes a finished clinical endpoint. Both describe a method for constructing a candidate endpoint.

Why deep learning often wins the internal accuracy contest

A conventional radiomics pipeline imposes a bottleneck. It compresses the MRI volume into predefined measurements. That can be an advantage when the measurements correspond to a plausible phenotype. It can also discard information that is difficult to encode with a finite feature library.

Deep learning can preserve more of the spatial signal. A convolutional architecture may distinguish a lesion core from an infiltrative margin, integrate information across T1-weighted, T2-weighted, FLAIR, diffusion, or perfusion inputs, and learn non-linear interactions among anatomical and intensity patterns. The network is not restricted to the texture families selected by the investigator.

That additional capacity can yield higher classification performance. Reviews of MRI neuroimaging applications have reported deep learning accuracy up to 98.2%, compared with 61–89% for classical radiomics approaches. The comparison is useful only if the datasets, labels, validation design, preprocessing, and endpoint definitions are comparable. Usually they are not.

Accuracy is also a blunt metric. It can conceal class imbalance. It does not establish calibration. It does not show whether errors are concentrated in a clinically important subgroup. For trial biomarkers, the relevant output may be a continuous risk estimate, treatment-response probability, time-to-event association, or longitudinal change. A classifier that performs well on a balanced retrospective dataset may be poorly suited to a primary trial endpoint.

Deep learning performance can also arise from acquisition fingerprints. Scanner vendor, field strength, sequence implementation, reconstruction kernel, site-specific positioning, or even patient motion may correlate with the label. The model detects a stable pattern in the training data. The investigator interprets it as disease biology. External validation then exposes the substitution.

High internal accuracy proves that a representation separates the available dataset. It does not prove that the representation measures the intended biology.

Radiomics has its own version of this problem. A feature may appear biologically meaningful while actually tracking voxel size, interpolation, intensity discretization, segmentation style, or denoising. A gray-level texture statistic is not a physical invariant. Change the acquisition or preprocessing pipeline and the feature can move even when the tissue does not.

The distinction is critical for quantitative MRI feature extraction. The computational pipeline must be treated as part of the measurement instrument. The scanner, pulse sequence, receive chain, reconstruction, normalization, segmentation, and feature calculation jointly define the biomarker.

Interpretability is not a cosmetic advantage

Clinical trial endpoints require more than predictive separation. Investigators need to know what the variable means, how it changes, and whether a change can be attributed to disease, treatment, or measurement noise.

Radiomics offers a narrower but more inspectable chain. The region of interest can be reviewed. The feature definition can be frozen. The investigator can quantify how feature values respond to resampling, intensity normalization, segmentation perturbation, and acquisition changes. This does not make the feature valid. It makes invalidity easier to detect.

Suppose a model uses a shape descriptor derived from a glioma segmentation. The descriptor may have a direct relationship to lesion geometry, but it remains dependent on the boundary. If edema, necrosis, enhancing tumor, and non-enhancing infiltrative tissue are segmented inconsistently, the feature becomes a segmentation biomarker as much as a disease biomarker.

Texture is more fragile. It depends on spatial resolution, noise, intensity scaling, gray-level binning, interpolation, and filtering. A feature that yields a strong association in one protocol may degrade after a change in slice thickness or reconstruction. The mathematical definition is explicit. The measurement conditions still constrain it.

Deep learning explanations are less direct. Saliency maps, occlusion tests, attention maps, feature embeddings, and counterfactual perturbations can indicate where the model responds. They do not necessarily identify a stable biological mechanism. An activation map is an audit instrument, not a causal explanation.

This matters when a trial sponsor claims that a deep learning imaging biomarker reflects tumor cellularity, vascularity, necrosis, or molecular status. The claim requires more than a heatmap. It requires correlation with pathology, molecular assays, quantitative imaging references, longitudinal behavior, or a prespecified clinical outcome.

The strongest deep learning studies therefore do not rely on visual explanations alone. They combine model outputs with reproducible acquisition, blinded external testing, calibration analysis, subgroup evaluation, and biological correlation. The network can remain mathematically complex. The validation framework cannot.

Glioma radiogenomics illustrates the difference

MRI radiomics has been used to predict molecular alterations in glioma without tissue sampling. Reported AUC values for IDH mutation prediction range from 0.80 to 0.99. For ATRX alterations, reported AUC values range from 0.76 to 0.97.

These ranges are clinically interesting and methodologically dangerous. They show that MRI contains information associated with molecular phenotype. They do not establish that every high-performing model has learned the same signal. Nor do they prove that a radiomics model can replace molecular testing.

A wide AUC range usually indicates heterogeneity in cohorts, definitions, imaging protocols, segmentation procedures, feature selection, and validation design. The upper boundary attracts attention. The range is the more important fact. It shows how strongly performance depends on context.

For a clinical trial, the correct question is whether the biomarker preserves discrimination and calibration across the intended enrollment environment. If a model is used to stratify patients by IDH status, the study must define how missing sequences, incomplete tumor coverage, postoperative changes, and uncertain molecular labels are handled. If the biomarker is intended for monitoring, the analysis must also establish whether the output changes consistently over time and whether that change is distinguishable from scanner or preprocessing drift.

A cross-sectional molecular prediction task and a longitudinal treatment-response endpoint are not the same problem. The first asks whether an image contains information associated with a label. The second asks whether a repeated measurement provides reliable evidence of biological or clinical change.

Multi-site MRI is where the comparison becomes real

A model that has not faced scanner variability has not faced deployment.

Multi-site trials introduce changes in field strength, vendor, gradient performance, coil configuration, pulse sequence timing, acceleration, partial Fourier sampling, motion burden, reconstruction software, and image export. These changes affect SNR, contrast, spatial resolution, geometric fidelity, and intensity distributions. They also alter the statistical environment seen by the model.

Radiomics exposes these effects through feature instability. Deep learning absorbs them into its learned representation, sometimes robustly and sometimes destructively. A high-capacity model may tolerate moderate variation if the training data span the relevant acquisition space. It may instead learn site identity as a shortcut.

Harmonization is not a single preprocessing command. It is a chain of decisions:

• Which sequences are mandatory, and which are optional?
• Are images resampled to a common voxel geometry?
• How is bias-field correction applied?
• Are intensities normalized within the brain, within tissue classes, or against a reference scan?
• Are scanner-specific features removed, modeled, or retained?
• Does harmonization operate before segmentation, after segmentation, or in feature space?
• Are test-site distributions visible during model development?
• Is the harmonization method itself frozen before external evaluation?

The answer can change the biomarker.

For radiomics, discretization choices and resampling settings must be locked. A change in bin width can alter texture values. A change in interpolation can alter boundaries and local spatial relationships. A different segmentation algorithm can shift shape and intensity features without any biological change.

For deep learning, the issue is broader. The input tensor may appear standardized while retaining acquisition-specific information. A model trained on one vendor’s contrast behavior can treat another vendor’s images as out-of-distribution even after nominal normalization. Domain adaptation can reduce this gap, but it can also remove disease-relevant variation if applied without control.

External validation must therefore be designed as a measurement challenge, not a ceremonial final split. The external cohort should represent the scanners, sites, protocols, demographic composition, and clinical workflow in which the biomarker will operate. If validation is performed only on images drawn from the same acquisition ecosystem as training, the result is closer to internal reproducibility than transportability.

Harmonization does not create biological invariance by declaration. It creates a new measurement pipeline that must itself be validated.

The endpoint also needs a prespecified handling strategy for failed or low-quality scans. Excluding difficult images after seeing model performance can bias the result. A clinical biomarker must tolerate the operational conditions of the trial, not an idealized subset of them.

Trial endpoints impose stricter requirements than diagnostic models

The phrase clinical trial endpoint carries operational consequences. A biomarker may be used for enrichment, stratification, prognostic modeling, pharmacodynamic monitoring, response assessment, or treatment assignment. Each use requires a different validation argument.

A diagnostic classifier can be evaluated through discrimination, calibration, and clinical utility. A trial biomarker may need repeatability, sensitivity to change, temporal stability, and a defined relationship to outcome. If the metric is intended to detect treatment effect, the analysis must show that the measurement is responsive without being dominated by acquisition noise.

Radiomics can be attractive for this purpose because a compact set of features can be frozen and audited. The investigator can track feature drift across visits. Repeat scans can estimate measurement error. A feature that yields a stable value under repeated acquisition has a stronger foundation than one selected solely for maximal single-visit classification.

Deep learning can also produce longitudinal biomarkers. A network may compare visits directly, encode temporal sequences, or generate an embedding from each scan. Its advantage is representational capacity. Its weakness is the difficulty of separating biological change from changes in scanner state, registration, positioning, motion, or sequence execution.

Longitudinal imaging studies need more than a model output at baseline and follow-up. They require a measurement model. The expected within-subject variation must be characterized. The interval between scans must be clinically meaningful. Registration errors must be quantified. Treatment-related imaging effects, including pseudoprogression or altered perfusion, must not be treated as generic signal shifts.

The endpoint definition should answer four technical questions:

1. What image-derived quantity is being measured?

2. What acquisition and preprocessing conditions are required?

3. What magnitude of change exceeds expected measurement variation?

4. How does that change relate to the prespecified clinical or biological outcome?

If the answer to the first question is a latent network score, the remaining questions become harder, not optional.

Hybrid models are a practical compromise, not a theoretical victory

Hybrid architectures combine handcrafted radiomics features with deep-learning representations. The objective is clear: preserve explicit quantitative descriptors while allowing the model to learn spatial patterns that predefined features may miss.

A hybrid model can concatenate radiomic features with neural embeddings, use radiomics to regularize the network, or apply deep learning to segmentation and radiomics to downstream prediction. It can also use handcrafted measurements as auxiliary outputs, forcing the network to preserve selected anatomical or intensity relationships.

This approach may improve the trade-off between classification performance and interpretability. It does not automatically solve domain shift. If both branches receive site-specific artifacts, the combined model can amplify them. If the radiomics branch is unstable under resampling and the neural branch is unstable under vendor change, fusion creates a larger audit surface.

The architecture should therefore be evaluated by layer:

• Image formation: acquisition, k-space sampling, gradient behavior, SNR, contrast, and reconstruction.
• Preprocessing: registration, denoising, bias correction, resampling, and intensity normalization.
• Localization: manual, semi-automated, or learned segmentation.
• Representation: handcrafted features, neural embeddings, or both.
• Prediction: classifier, regression model, survival model, or treatment-effect estimator.
• Validation: internal split, temporal test, site-held-out test, and prospective evaluation.
• Clinical interpretation: biological correlation, repeatability, calibration, and endpoint utility.

This layered audit prevents a common error: attributing a failure at the endpoint level to the model architecture when the actual source is unstable segmentation or acquisition drift.

A hybrid model is useful when its components have distinct jobs. The radiomics branch can provide defined measurements. The neural branch can capture distributed spatial information. The final endpoint must still be interpretable in terms of repeatability and clinical purpose.

What should a biomarker development program choose?

The choice between radiomics and deep learning should follow the study design, not the fashion cycle.

Radiomics is a strong candidate when the cohort is limited, the target region can be defined reliably, the feature definitions are biologically defensible, and the trial requires transparent measurement behavior. It is particularly suitable when investigators need to inspect feature stability across scanners and visits. Its explicitness makes failure visible.

Deep learning is a strong candidate when the dataset is sufficiently large and heterogeneous, the imaging phenotype is spatially complex, and manual feature design would impose a substantial information bottleneck. It can yield higher discrimination and exploit multimodal image context. Its use demands stronger controls against shortcut learning and domain shift.

A practical selection framework is more specific than choosing the model with the best validation accuracy:

• Use radiomics when the endpoint must be expressed through defined, auditable image properties.
• Use deep learning when the phenotype is distributed across spatial context or multiple sequences and the training data cover the acquisition variability.
• Use a hybrid model when explicit measurements and learned representations answer different parts of the biological question.
• Reject any approach whose validation depends only on a random split from a single site.
• Require repeatability analysis when the biomarker will be measured longitudinally.
• Treat segmentation, intensity normalization, and resampling as endpoint components.
• Report external performance separately from internal performance.
• Preserve an analysis pipeline that can be rerun when the scanner, software version, or sequence protocol changes.

The final decision should also account for deployment constraints. A model that requires a fixed sequence bundle unavailable at participating sites is not a trial biomarker. A radiomics pipeline that cannot reproduce its discretization and segmentation settings is not an auditable measurement. A neural network that fails silently on missing modalities is not robust software.

The measurement comes before the model

Radiomics versus deep learning for MRI biomarkers is often presented as a contest between interpretability and accuracy. That framing is incomplete. The deeper issue is measurement validity under physical and clinical variation.

Radiomics constrains the representation early. Deep learning constrains it late, through data and optimization. Both approaches can identify clinically relevant signal. Both can learn scanner-specific artifacts. Both can produce impressive retrospective metrics that do not survive external validation.

For MRI trial biomarkers, the decisive standard is not whether the algorithm is classical or neural. It is whether the output remains stable, transportable, biologically associated, and responsive to the clinical process the trial intends to measure.

A classifier can be accurate and still be unusable. A handcrafted feature can be interpretable and still be non-reproducible. A hybrid architecture can improve performance and still inherit the weaknesses of both branches.

The scanner is a signal processor. The biomarker is a claim about that signal. If acquisition variability, reconstruction behavior, preprocessing, and validation design are not controlled, the claim is not yet clinical evidence. It is only a model result.