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Designing deep learning studies in cancer diagnostics


The number of publications on deep learning for cancer diagnostics is rapidly increasing, and systems are frequently claimed to perform comparable with or better than clinicians. However, few systems have yet demonstrated real-world medical utility. In this Perspective, we discuss reasons for the moderate progress and describe remedies designed to facilitate transition to the clinic. Recent, presumably influential, deep learning studies in cancer diagnostics, of which the vast majority used images as input to the system, are evaluated to reveal the status of the field. By manipulating real data, we then exemplify that much and varied training data facilitate the generalizability of neural networks and thus the ability to use them clinically. To reduce the risk of biased performance estimation of deep learning systems, we advocate evaluation in external cohorts and strongly advise that the planned analyses, including a predefined primary analysis, are described in a protocol preferentially stored in an online repository. Recommended protocol items should be established for the field, and we present our suggestions.


Deep learning facilitates utilization of large data sets through direct learning of correlations between raw input data and target output, providing systems that may use intricate structures in high-dimensional input data to accurately model the association with the target output1,2. Numerous studies have reported on the applicability of deep learning in cancer diagnostics, including prediction of diagnosis, prognosis and treatment response3,4,5. Although many of these tools are claimed to perform comparably with or better than clinicians, few have yet demonstrated real-world medical utility6. This is partly a natural consequence of the time needed for evaluating and adapting systems affecting patient treatment. However, many studies evaluating apparently well-functioning systems are at high risk of bias6. Of particular concern is the frequent lack of stringent evaluation of external data7,8 and that some systems are developed or evaluated on data that are too narrow or inappropriate for the intended medical setting9,10,11,12. Thus, the lack of a well-established sequence of evaluation steps for converting promising prototypes into properly evaluated medical systems clearly limits the medical utilization of deep learning systems.

Whereas supervised machine learning techniques traditionally utilized carefully selected representations of the input data to predict the target output, modern deep learning techniques use highly flexible artificial neural networks to correlate input data directly to the target outputs1,2,13. The relations learnt by such direct correlation will often be true but may sometimes be spurious phenomena exclusive to the data utilized for learning. In fact, the millions of adjustable parameters make deep neural networks capable of performing perfectly in training sets even when the target outputs are randomly generated and, therefore, utterly meaningless14. Thus, the high capacity of neural networks induces serious challenges on how to design and develop deep learning systems, and on how to validate that such a system performs adequately in the intended medical setting15. Adequate clinical performance will only be possible if the system has good generalizability to subjects not included in the training data16,17.

The design challenge involves issues related to selection of appropriate training data, such as representativeness of the target population (Box 1), as well as modelling questions such as how the variation of training data may be artificially increased without jeopardising the relationship between input data and target outputs in the training data18,19. The validation challenge includes verifying that the system generalizes well, for example performs satisfactorily when evaluated on relevant patient populations at new locations and when input data are obtained using differing laboratory procedures or alternative equipment15,16. Moreover, deep learning systems are typically developed iteratively, with repeated testing and often including various selection processes that may bias results20. Similar selection issues have been recognized as a general concern for the medical literature for many years21,22. Thus, when selecting design and validation processes for diagnostic deep learning systems, one will have to focus both on the generalization challenges and on preventing ‘classical’ pitfalls in data analysis. We will, however, argue that both sets of challenges may be diminished by adopting certain fairly simple principles partly borrowed from the drug clinical trial field.

In this Perspective, we first describe the validation challenges with focus on the use of external cohorts. An evaluation of presumably influential deep learning studies is used to reveal the status of the field particularly with respect to validation procedures. We then consider generalization issues, especially looking at the importance of both natural and artificially induced variations in training data sets. In the last part, we highlight the importance of evaluating an external cohort according to a predefined primary analysis to reduce selection bias, and we outline a suggested sequence of evaluation steps for deep learning studies in cancer diagnostics, including the use of protocols with predefined analysis plans.

External cohort evaluation

Rigorous performance evaluation is particularly important due to the inherent high complexity of deep neural networks, as seemingly well-performing deep learning systems might utilize unintentional and possibly false features10,11,12 and respond unexpectedly to apparently irrelevant changes of the input data23. Failure to properly evaluate systems might have far-reaching consequences, including misdirection of further research, diminished credibility of research findings and, most importantly, being worthless or even harmful to patients if used to influence treatment24,25.

The importance of an external cohort evaluation

As an initial evaluation step, the cohort used for development of a deep learning system is often partitioned randomly into three distinct subsets, hereunder referred to as ‘training’, ‘tuning’ and ‘test’, where the training subset is applied to learn candidate deep learning models, the tuning subset to select the deep learning system that appears to perform best and the test subset applied to evaluate the performance of the selected system8. The evaluation of the test subset may provide unbiased estimation of the performance in the development cohort. It may also provide some information on the system’s ability to perform well in other populations by considering the extent to which the system performs better on the training subset than on the test subset, as this indicates the level of overfitting to the training data. Systems that are highly overfitted to the training data are likely not to perform well on other populations as the noise utilized to improve the performance on the training subset may negatively influence the performance on other populations. However, even a system that performs similarly in training and test subsets might perform far from acceptably on cohorts distinct from the development cohort26,27. As discussed below and in Box 1, this may be caused by the system utilizing data features that correlate with the target outcome only in the development cohort, which could be viewed as overfitting to the entire development cohort, or might also be caused by important predictive features not being adequately represented in the development cohort. Thus, using a random subset of the development cohort for testing does not imply that the results have external validity, that is, the performance of the system observed in the test subset may not generalize to patients external to the development cohort.

For example, Zech et al.11 investigated a deep learning system for detection of pneumonia on chest X-ray images and found that it was not able to uphold the high discrimination performance achieved in the development cohort when applied to cohorts from different institutions. In this case, there was a substantially higher disease prevalence in one of the training cohorts, and it appears that the poor generalization was in part caused by utilization of cohort-specific characteristics. In particular, the system utilized metallic tokens that radiology technicians placed on patients to indicate laterality, as these often appeared differently in different cohorts. The authors further point out that the system might not even generalize well to other patients from the same institution as the development cohort, because some correlations between input data and target outcome in the development cohort may not be present in new cohorts from the same institution. Winkler et al.12 found that, for their system, visible surgical skin markings present in the image were associated with a higher prediction score for melanoma. Similarly, Narla et al.10 reported that the presence of a ruler beside a lesion in an image was associated with a higher malignancy score for skin cancer. Of course, neither skin markings nor rulers are causing the skin cancer, but the apparent correlation present in the development cohort is sufficient for the deep learning system to make use of these associations. It could be argued that more thorough quality control on the training data could mitigate this, but it is highly unlikely that one is able to detect and control for all potential confounding factors present in the training set.

Thus, unbiased performance estimation in a real-world application of a deep learning system requires external cohorts representative of a target population22,28,29,30. In an external validation, no information from the external cohort should have influenced the design of the system or the estimation of any model parameter. Additionally, the external cohorts will implicitly define the patient population for which we have estimated the performance of the system. Thus, to know whether or not the results may be generalized to the entire target population, we need a broad validation where the cohorts may be regarded as representative of this desired target population, for example with respect to age, sex, ethnicity, geographical differences and disease prevalence31,32. Other types of evaluations may also be warranted prior to introducing the system in medical practice, including so-called domain validation to evaluate whether the system performs consistently across a range of laboratories and technical equipment (Box 2).

Objective, non-random separation of patients from the same hospital or subjects from the same country — for example, distinguishing between patients treated before and after a certain date — allows using one cohort for training and tuning, and another for what has been denoted ‘narrow validation’22 (Box 2). Such evaluation might provide unbiased performance estimation for a particular hospital. However, the two cohorts should not simply be a non-random separation of an originally larger cohort but, instead, be processed separately when acquiring data and ascertaining target output33. Narrow validation is sometimes considered a limited type of external validation22.

Prevalence in recent studies

In order to investigate the prevalence of external cohort evaluation and other characteristics of recent studies on deep learning and cancer diagnostics, we searched PubMed on 21 April 2020 for original research articles published in 2015 or later (Supplementary Methods). The search provided 3,578 results, and the number of publications roughly doubled each year since 2016. To explore the use of external cohort evaluation and other characteristics in some of the most prominent and perhaps best studies, we restricted our evaluation to those with at least 20 citations per year or published in a journal with an impact factor of 10 or larger. Although studies satisfying either of these criteria are presumably quite influential, we acknowledge that some of the other studies might be equally good. In particular, recent studies may not have had time to accrue 20 citations even if they are currently of great interest, and such studies would only be included if published in a journal with an impact factor of 10 or larger. This will exclude most studies published in new journals that are expected to receive impact factors of 10 or larger when these become available. However, we consider the selected papers to be sufficient for the purposes of this discussion, as they show that some aspects of study design could be better even in some of the presumably best studies. Only 257 (7%) of the 3,578 search results satisfied at least 1 of these selection criteria, and another 43 search results were excluded because the document type in Web of Science indicated that these were not original research articles. The remaining 214 studies were manually evaluated (Supplementary Table 1). We further excluded 6 studies that were not original research articles and 102 studies where deep learning was not used to predict or classify features relevant for cancer diagnosis, prognosis or treatment response, or such potential utility of the deep learning system was not evaluated. After also excluding 14 studies without human subjects or only pertaining to cell biology, we ended up with 92 eligible studies34,35,36,37,38,39,40,41,42,43,44,45,46,47,48,49,50,51,52,53,54,55,56,57,58,59,60,61,62,63,64,65,66,67,68,69,70,71,72,73,74,75,76,77,78,79,80,81,82,83,84,85,86,87,88,89,90,91,92,93,94,95,96,97,98,99,100,101,102,103,104,105,106,107,108,109,110,111,112,113,114,115,116,117,118,119,120,121,122,123,124,125, of which 85 (92%) used images as input to the deep learning system34,35,36,37,38,39,40,41,42,43,44,45,46,47,48,49,50,51,52,53,54,55,56,57,59,60,61,62,63,64,66,67,69,70,71,72,73,74,75,76,77,78,79,80,81,82,83,84,85,86,87,88,89,90,91,92,93,95,96,97,98,99,101,102,103,104,105,106,107,108,109,110,111,112,113,114,115,116,117,118,119,120,121,123,125.

Among 516 original research articles on artificial intelligence for diagnostic analysis of medical images published in 2018, Kim et al.7 found only 31 studies (6%) that evaluated an external cohort. By contrast, 50 (54%) of our 92 eligible studies evaluated the performance of the deep learning system on an external cohort37,40,48,49,51,53,55,60,62,63,65,70,73,74,75,78,79,80,82,83,84,85,86,87,90,92,93,95,96,98,100,101,102,104,105,106,107,108,109,110,111,112,113,114,115,116,120,121,123,125. This discrepancy is most likely mainly attributed to our selection of presumably influential studies and partly attributed to the increasing usage of external cohorts (Fig. 1a); 34 (72%) of the 47 eligible studies published in 2019 and 2020 evaluated an external cohort compared with 9 (39%) of the 23 eligible studies published in 2018 and 7 (32%) of the 22 eligible studies published before 2018.

Fig. 1: Characteristics of recent, presumably influential, deep learning studies in cancer diagnostics.

a | Percentage of studies reporting on the evaluation of a broad or narrow cohort (Box 2) by year of publication, for all 92 eligible studies. b | Percentage of studies specifying 1, multiple or no primary performance metrics in the analysis of the external cohort, for the 50 eligible studies that reported on the evaluation of an external cohort. c | Percentage of studies specifying a predefined analysis of the external cohort, for the 50 eligible studies that reported on the evaluation of an external cohort. Studies that specified predefined analyses of external cohorts without defining which was the primary, if any, were categorized as ‘predefined analyses’. Studies with a predefined primary analysis were categorized according to whether the primary analysis was pre-specified in a protocol or not.

Among studies satisfying both of our selection criteria, 79% (11 of 14) evaluated an external cohort, compared with 68% (25 of 37) for studies that satisfied only the impact factor criterion and 34% (14 of 41) for studies that satisfied only the citation frequency criterion. It thus appears that journals with a high impact factor have a preference for studies evaluating external cohorts. This is consistent with the call by editors of leading scientific journals for rigorous evaluation of artificial intelligence tools126,127 and explicit prioritization of biomarker studies that evaluate external cohorts by some journals, for example Journal of Clinical Oncology.


Although increased use of external cohorts is an important step towards proper validation of deep learning systems, one is still left with the challenge of ensuring that the results obtained for such a population provide a satisfactory measure of the performance within the entire intended target population. This target population may typically be patients who have a specific cancer type, and although often restricted, for example, to certain stages of the disease, the target population is normally broad. Although some studies may use more than one external cohort and some use trials with many centres distributed over several countries, it is difficult to obtain external cohorts that entirely cover the target population. Thus, successful application of a deep learning system will depend on good generalization properties, so that good performance on one population also indicates satisfactory performance on populations differing with respect to some properties. Fortunately, exploring generalization in deep learning is an active research area128, and by utilizing certain design principles, deep learning systems have shown remarkably good generalization performance on numerous tasks2,3,4,5.

One way of increasing generalization is to control the neural network’s capacity to express complex mappings, for example by limiting the number of adjustable parameters in the network, imposing various constraints on the network or regularizing the optimization129,130. Transfer learning could also increase generalization, particularly when training data for the task at hand are scarce131,132. In transfer learning, the network is initialized with parameters optimized using data for a different task, typically using large data sets such as ImageNet133,134, which may mitigate overfitting at the possible cost of introducing biases135,136,137. Making the training data set more diverse and more representative of the target population is another way of increasing generalization138. Of particular importance is to ensure adequate and unbiased representation across demographic characteristics such as sex, race and ethnicity (Box 1). In addition to expanding the natural training data set, that is, the set of training data acquired from a range of patient samples with associated target outcome, one may artificially augment the training data set by applying smaller transformations on the inputs while maintaining their relationship to the target output18,139. This can reduce the network’s ability to memorize details of the training data and thereby increase generalization, especially in situations where the availability of training data is limited. The transforms can randomly change, often called ‘distort’, the input data by, for example, adding noise, erasing parts, shifting and scaling colours or altering the image geometry19. Artificially diversifying the training data may increase generalization by enabling the resulting system to ignore vagaries of the measurement process and even become applicable to multiple data acquisition procedures, for example different acquisition equipment140,141. Other augmentation techniques include those that generate artificial input data, for example by mixing multiple data inputs19. The value of augmentation techniques has been observed in various application domains19, including use on images obtained from radiology38,142,143,144 and histopathology141,145.

To illustrate the importance of the amount of and variation in training data, and more specifically show how data distortion may work to improve deep learning systems in cancer diagnostics, we show this type of analysis here using data from a previously published study113. This previous study applied deep learning to predict colorectal cancer-specific survival directly from conventional haematoxylin and eosin-stained sections, with training and tuning data derived from 2,473 patients from four cohorts. The performance was evaluated on an external cohort consisting of 1,122 patients from a randomized controlled trial of a drug that was observed to not affect survival146. We applied the convolutional neural network called Inception-v3 (ref.147), which is a network commonly used in medical image diagnostics8, in both the previously published analyses and the new analyses presented here.

Initially, we applied the same distortion process as in our published analyses113. This process artificially increased the variation of the training images by randomly distorting their colours, which is an augmentation technique that appears crucial when training deep learning systems in histopathology145. Initially, the maximum amount of distortion we allowed was quite modest (Fig. 2a). To illustrate the effect of reducing the number of patients while keeping the patient heterogeneity implied by having data from four cohorts, we randomly sampled 979 patients in such a manner that the data had the same number of training and tuning patients with and without cancer-specific death as in the cohort from the Gloucester Colorectal Cancer Study, UK (the largest of the four training and tuning cohorts). The decreased performance of the resulting deep learning system when evaluated on the external cohort (Fig. 2b) exemplifies the importance of a large natural training data set and its intrinsic variation138. Further reduction of the number of patients decreased the performance further; training and tuning on a quarter of the 979 patients or fewer (that is, fewer than 250 patients) provided systems that did not perform substantially better than random guessing (Fig. 2b).

Fig. 2: Effect of data variation when training deep learning systems.

For each analysis set-up, 20 individual deep learning systems were trained and tuned for prediction of colorectal cancer-specific survival using images of haematoxylin and eosin-stained sections acquired by both Aperio AT2 (Leica Biosystems, Germany) and NanoZoomer XR (Hamamatsu Photonics, Japan), as in the previously published analyses113. The individual systems were applied to evaluate the external cohort using NanoZoomer XR slide images, and the concordance index (c-index) of the system’s binary output was computed. Standard box plots were made using Stata/SE 16.1 (StataCorp, USA). The matched random subset contained the same number of training and tuning patients with and without cancer-specific death as in the Gloucester cohort, in total 979 patients. a | An example image from the training data set and the results of applying the maximum possible amount of colour distortion at each step in the random distortion process used in the published Inception-v3 analyses113. Generally, the distortion process applies random colour distortions to an image by converting the image to HSV colour space, adding a random value between –0.05 and 0.05 to the hue, scaling the saturation by a random value between 1/1.1 and 1.1, adding a random value between –0.1 and 0.1 to the saturation, scaling the brightness (or, technically, the value channel in the HSV colour space) by a random value between 1/1.1 and 1.1, adding a random value between –0.1 and 0.1 to the brightness and converting back to RGB colour space. Intuitively, the leftmost and rightmost images represent the range of the random colour distortion, that is, the minimum and maximum possible amount of colour distortion for the applied distortion process, where the minimum is no colour distortion. Scale bar, 100 µm. b | Effect of changing the number of patients in the training and tuning subsets when using the original amount of colour distortion, as depicted in part a. c | Effect of changing the amount of colour distortion when training and tuning using the matched random subset. Label ‘0’ on the horizontal axis identifies deep learning systems trained without any colour distortion, label ‘1’ identifies systems trained with the colour distortion process depicted in part a and label ‘4’ identifies systems trained with the colour distortion process depicted in part d. d | Similar to part a, but four times the amount of colour distortion was used at each step in the distortion process. Scale bar, 100 µm. e | Effect of changing the amount of colour distortion and the number of patients and cohorts in the training and tuning subsets.

We then showed that modifying the distortion process may mitigate for the performance loss observed when reducing the number of patients in training and tuning. Compared with using all 2,473 patients for training and tuning, using 979 randomly selected patients and four times the original amount of colour distortion provided similar performance on the external cohort (Fig. 2c). For this modified distortion process we allowed quite substantial colour distortions (Fig. 2d), and the results showed that artificial augmentation may, in some cases, compensate for limited natural training and tuning data. However, increasing the amount of colour distortion further provided worse performance (Fig. 2c), illustrating the trade-off between preventing overfitting through random distortions and occluding relevant information for the prediction task.

Randomly sampling 979 patients from all four cohorts maintained much of the variation in the natural training and tuning data. If we instead used only the Gloucester cohort, which contained the same number of training and tuning patients with and without cancer-specific death as in the random sample, we obtained worse performance on the external cohort, most clearly when including more colour distortion in training (Fig. 2e). This underlines the importance of designing studies such that the natural training data are diverse, and Fig. 2e additionally illustrates that natural variation and artificial variation work well together to increase generalizability.

In general, the most suitable distortion process will depend on the particular medical prediction task because the involved data will tolerate different amounts of the various types of distortions before true correlations between input and target output are occluded. For instance, deep learning systems that classify based on images of skin lesions or tumour sections are likely to benefit from being invariant to rotations, whereas systems aimed at supporting radiology might rely on the orientation in images of larger organ structures and, thereby, perform worse if forced to be rotation invariant. Thus, the distortion process needs to be fine-tuned to the particular application, as findings about which distortion process appears most beneficial in one scenario — for example, findings from the example presented in Fig. 2 — are not necessarily directly applicable to other scenarios. However, the general principle is that including much and varied training data is important. As the importance of artificial augmentation decreases with the amount and diversity in the natural training data, prediction tasks where the true correlations between input data and target output are easily obscured by distortion warrants a more comprehensive natural training data set.

Predefined primary analysis

In the development of a deep learning system, researchers will often evaluate different systems sequentially, each time having the possibility to learn from interpreting the previous evaluations and adapt the system to the specific data used for evaluation. Such repeated evaluations will bias the estimates, and their dependence on previous evaluations makes established statistical approaches for adjusting for multiple comparisons not applicable148,149. Similar reanalysis issues may arise if the initial analysis of a specific deep learning system reveals issues that are then corrected and the performance is re-evaluated. Such problems of repeated or multiple evaluations are well-known from examinations of the data analysis in various types of published medical studies, and have been identified as important contributors to biased inference and irreproducible results20,150.

As discussed above, evaluation of an external cohort is required for unbiased performance estimation in a real-world application of the deep learning system, but this is only a prerequisite as multiple or repeated evaluations may cause bias even if evaluating an external cohort. Great caution would therefore be needed when interpreting studies that report multiple analyses without specifying which was initially planned to be the primary analysis, if any.

Prevalence of predefined primary analysis

In our evaluation of recent, presumably influential, deep learning studies in cancer diagnostics, all studies performed multiple analyses of the external cohort typically in the form of evaluating multiple systems, analysing multiple subpopulations or using various analysis methods. Only 3 (6%) of the 50 eligible studies that evaluated an external cohort used one of the well-established methods for adjustment for multiple comparisons51,62,114, for example Bonferroni correction. This implies that most studies should have specified which analysis was considered the primary analysis prior to evaluation of the external cohort, if such a decision was made, in order to inform the reader which analysis was not affected by selection bias and to help distinguish studies with a predefined primary analysis from those that repeatedly evaluated the external cohort and might have ended up reporting severely biased performance estimates. Although the principle of using an external data set only once to evaluate the final hypothesis should be well-known in the machine learning community151,152, it seems, currently, that there is no tradition for specifying the predefined primary analysis in deep learning publications other than those reporting on clinical trials. In our evaluation, 20 (40%) of the 50 studies evaluating an external cohort specified one or more primary performance metrics55,60,73,82,83,85,86,93,98,102,105,108,109,110,113,115,116,120,121,125 (Fig. 1b), but only 8 (16%) of the 50 studies specified a predefined primary analysis73,83,102,105,109,113,120,121 (Fig. 1c).

Pre-specification of the primary analysis has previously been advocated in diagnostic and prognostic research153,154, but this is unfortunately still not common practise despite being the only direct protection against selection bias20. To ensure unbiased estimation, the primary analysis should be unequivocally specified prior to all investigations that could reveal correlations between input data and target output in the external cohort. This would require the researchers to define all relevant aspects of the validation prior to analysing the cohort, including the deep learning system, target output, and patient and input data in the external cohort. Predefining the primary analysis will entail a commitment to the main analysis, which implies that the analysis should be carefully planned in advance and that researchers will be discouraged from performing creative data dredging155.

Choosing the primary metric

Many medical questions are categorical in nature, for example whether tumour or not, whether mutated or not and whether to offer treatment or not. However, deep learning models often output continuous values reflecting the predicted probability of each possible outcome. In such cases, the predefined primary analysis should preferably evaluate a categorization of the model output aimed at answering the medical question. The primary analysis will then be comparing predicted and target outcome in the external cohort, for example by measuring the so-called balanced accuracy156. Measuring the performance using categorical outputs often provides more conservative estimates157 and avoids issues with metrics frequently applied to measure the performance using continuous outputs. For instance, the area under the receiver operating characteristic curve (AUC)158 and the concordance index (c-index)159 are only affected by the ranking of the continuous outputs, not the prediction scores themselves160. Thus, such metrics may indicate that a deep learning system performs well even if it predicts markedly too high probabilities for all patients in a specific cohort, provided that the continuous outputs of the system rank the patients in a fairly correct order. In another cohort, the same system may similarly appear to perform well even if it predicts markedly too low probabilities for all of those patients. The generalizability of such a system is poor, yet this would not be evident from the AUC and c-index of the continuous outputs but would be evident from the AUC and c-index of a categorization defined irrespective of the external cohorts. The categorization may be defined by, for example, determining suitable thresholds during tuning or selecting the outcome with the highest prediction score as the predicted outcome. Defining the categorization using the external cohort, even at predefined levels of, for example, sensitivity, adapts the categorical marker to the specific external cohort and may occlude shifts in the prediction scores as with the AUC and c-index of the continuous outputs.

In our evaluation of recent, presumably influential, deep learning studies in cancer diagnostics, we found that 34 (68%) of the 50 studies evaluating an external cohort reported the estimated performance of a categorical marker on the external cohort, with a categorization defined irrespective of the external cohort48,49,53,55,60,62,63,65,73,75,78,79,80,82,85,87,90,98,100,102,104,105,106,108,109,110,111,113,114,115,116,120,121,125. The proportion was lower for studies reporting on deep learning systems that used histopathology section images as input, with only 6 (40%) of 15 studies evaluating a fixed categorical marker on the external cohort48,55,82,111,113,114, which is surprising as most histopathological evaluations provide categorical values.

For certain deep learning systems, the intended medical application directly utilizes the system’s continuous output, for example to triage patients for further examinations, and in such cases the continuous output should be evaluated in the primary analysis. This may warrant additional analyses to reveal generalization issues that might be occluded by the selected performance metric, for example to consider a calibration plot in addition to the c-index when evaluating a clinical decision support system for predicting patient outcome22,26. In general, the metric chosen for the primary analysis should be one that measures how well the deep learning system performs in the intended medical application. For instance, the overall performance in a classification task could be measured using the balanced accuracy.

From conception to application

All research with the potential to influence patient treatment should undergo careful evaluation sequences and be driven by protocols with a predefined statistical analysis plan153. Figure 3 illustrates what we consider natural and important steps in the development and evaluation of deep learning systems for medical applications.

Fig. 3: Development and evaluation of deep learning systems.

A deep learning project often begins with testing a conceptual idea using pilot software based on a related open source implementation and data easily available to the researchers. Successful level I studies will typically evolve into explorative testing of different modelling options that might be more suitable for the particular task. The system that appears to perform best should be determined in a level II study that includes sufficient amount and variation in the natural training data set. Although performance estimates obtained in such studies are often inflated by the use of a subset that closely resembles the training subset, level II is an important step in the evaluation sequence that could motivate investigators to pursue evaluation of external cohorts and attract collaborators. As the lack of predefined primary analysis often entails post hoc adjustments influenced by the performance in the external cohort, we distinguish between studies without (level III) and with (level IV) a primary analysis unequivocally specified prior to all investigations that could reveal correlations between input data and target output in the external cohort. If the medical validity of a deep learning system is established in level IV studies, the indicated medical utility should be prospectively evaluated in randomized phase III clinical trials where the system directly intervenes with the current standard of care. If medical utility is demonstrated and necessary governmental agencies approve routine medical application, the system can be applied in medical practice while monitoring the long-term benefits, harms and costs of its application.

The initial exploratory studies aim to answer whether deep learning appears suitable for the task at hand or whether further investigations based on deep learning are not warranted at this time, usually because the hypothesis seems ill-founded or the available data are not expected to provide a system with adequate performance. The performance estimates obtained in such pilot studies are frequently inflated by the use of a limited development cohort, but promising findings may motivate further investigations. After a series of explorations, and possibly expansions, of the development cohort, the development should conclude by deciding which system appears to perform best on the intended medical task, considering also the sensitivity to vagaries of the measurement process. Of particular importance to prevent selection of a system that performs much worse on patients outside the development cohort, the study could include a sufficient amount and variation in the natural training data set and use techniques such as data distortion to increase the variation artificially.

There is growing interest in explainable deep learning systems161,162,163, including the creation of inherently more explainable systems and post hoc explanations of existing systems164. For image classification tasks in particular, so-called saliency maps visualize the contribution of each pixel to the final prediction score and can be created using numerous different techniques165,166,167. By increasing the transparency, the more explained systems might have more predictable generalizing abilities. This may be used to identify target populations within which the system is expected to generalize well or settings where the system is prone to fail. For example, Winkler et al.12 used such a technique to support their finding that surgical skin markings unduly increased the system’s prediction score for melanoma. Although current explainability techniques might suggest generalizability, and thereby suggest suitable target populations or influence the selection of which system to evaluate further, they will only provide indications and, thus, not reduce the need for proper validation.

Whereas efficacy studies of pharmaceutical products are usually preceded by prospective trials to estimate basic features such as safety and dosing168, deep learning systems for diagnostic purposes can to a larger extent utilize retrospective cohorts, for example from earlier clinical trials or medical practice. Given the risks, time frame and costs of interventional research168,169,170, we recommend rigorous, retrospective analyses to evaluate the medical validity of a deep learning system by conducting an external validation according to a predefined primary analysis. The results of such studies provide valuable information to direct further research, thus warranting publication regardless of the significance of the findings, which would also mitigate publication bias.

Rigorous, retrospective analyses of a deep learning system might warrant conducting a prospective, randomized phase III clinical trial where the system directly intervenes with the current standard of care in order to evaluate the system’s medical utility in a specific real-world application, considering both benefits and harms for patients in the target population30,171. Systems demonstrated to have medical utility and approved by necessary governmental agencies can be applied in medical practice while monitoring the long-term benefits, harms and costs for each specific real-world medical application in phase IV clinical trials. Such surveillance might eventually indicate that the system needs to be updated because of changes in medical practice or data acquisition172.

The levels of deep learning studies depicted in Fig. 3 and the phases of clinical trials were used to categorize recent, presumably influential, deep learning studies in cancer diagnostics in relation to the reliability of the performance estimation approach and the demonstrated applicability of the system in medical practice. Although some group sizes are very small, there appear to be notable differences between research fields defined by the input to the deep learning system (Fig. 4). The proportion of studies evaluating an external cohort was lowest for the 7 studies with only non-image inputs, such as omics data (29%; 2 of 7 studies), and highest for the 22 studies with images other than histopathology section and radiology images as input, for example from gastrointestinal endoscopic examinations or dermoscopic images (64%; 14 of 22 studies). Five (23%) of the 22 studies with other images as input even had a predefined primary analysis of the external cohort73,102,105,109,121, which included the 3 studies reporting on a randomized clinical trial, all of which evaluated a deep learning system to aid gastrointestinal examinations102,105,121.

Fig. 4: Reliability of performance estimations in recent, presumably influential, deep learning studies in cancer diagnostics.

Percentage of studies categorized in the different levels of deep learning studies or phases of clinical trials depicted in Fig. 3 for all 92 eligible studies separated by type of input to the neural network. The input was histopathology section images in 23 (25%) of the studies (part a), radiology images in 40 (43%) of the studies (part b), other images in 22 (24%) of the studies (part c) and other types of input in 7 (8%) of the studies (part d).

Recommended protocol items

When planning to evaluate the medical validity of a deep learning system through rigorous, retrospective analyses, we recommend the unequivocal specification of the predefined primary analysis to be documented in a study protocol. Relevant items in such protocols would differ from clinical trial protocols, which are the target of guidelines such as SPIRIT (Standard Protocol Items: Recommendations for Interventional Trials)173 and its extension to artificial intelligence174. Protocols should be developed before conducting the validation, and relevant items would therefore also differ from those in original research articles, which are the target of many reporting guidelines such as CONSORT (Consolidated Standards of Reporting Trials)175 and TRIPOD (Transparent Reporting of a multivariable prediction model for Individual Prognosis Or Diagnosis)22 as well as their extension or anticipated adaption to machine learning176,177. There is therefore a need to establish guidelines dedicated to study protocols describing validations of deep learning systems. We propose a non-exhaustive list of items that we consider essential in such protocols, termed Protocol Items for External Cohort Evaluation of a deep learning System (PIECES) in cancer diagnostics.

In order to be sufficiently concrete about the predefined primary analysis, the protocol needs to describe the deep learning system and how it will be assayed; define the external cohort, including its origin, what it represents in terms of medical setting and target population, and input data and target output; and clearly specify the performance evaluation. These three parts of the protocol form the basis of our PIECES recommendations together with a declaration of status (Box 3). The status declaration should scrupulously elucidate any investigations performed before finalising the protocol that could reveal correlations between input data and target output in the external cohort, or state that no such investigations were performed.

The PIECES recommendations are designed to facilitate identification of ambiguities and disagreements between the researchers planning to conduct an external validation as well as to provide a clear description of the predefined primary analysis as a reference for all readers, which may aid medical professionals in identifying well-designed studies and their applicability to their own clinical practice. The thought and work that should go into making such a protocol could also allow the researchers to make appropriate changes prior to performing the external validation. For instance, considering what the external cohort is intended to represent and how the deep learning system is envisioned to be applied in practice could affect the inclusion and exclusion criteria for patients and samples as well as the metric or statistical test applied in the primary analysis.

Researchers conducting an external validation would often like to perform multiple, related analyses to elucidate the performance of the deep learning system. To separate pre-planned analyses from exploratory, post hoc analyses, the PIECES recommendation encourages specification of predefined secondary analyses that the researchers would like to commit themselves to report on publication of their findings. Such secondary analyses would be affected by the multiple comparisons problem, but predefining and reporting all secondary analyses would provide a transparency that would substantially increase the credibility of the results. Importantly, the specification of predefined secondary analyses does not diminish the validity of the predefined primary analysis. Any analyses the researchers consider reporting, but do not wish to commit themselves to report, should not be specified as secondary analyses in the protocol and therefore should be reported as exploratory analyses, even though they might be thought of prior to analysing the external cohort.

Study registration

We recommend registration of the study protocol in an online repository before analysing the external cohort. Most major trial registries, for example and the International Standard Randomized Controlled Trial Number (ISRCTN) registry, accept registration of diagnostic accuracy studies154. These registries can be used to record external validation studies in deep learning, but some items will not be relevant and some important items, such as defining the deep learning system, will not be encouraged. A dedicated repository to register the study protocol describing the external validation of a deep learning system is therefore warranted. We recognize that it may be undesirable to publish a detailed study protocol in an online repository prior to conclusion of the study as this would reveal novel work prior to publication of the results and perhaps in some rare cases jeopardise publication. In a dedicated repository, a submission could be partially or completely invisible to the public and the protocol encrypted until the authors choose to reveal the submission and provide the required decryption key, thus facilitating preregistration of study protocols without requiring authors to reveal novel ideas prematurely.

Registration of observational studies has been advocated by editors of major clinical journals178,179, many editorial board members180 and researchers181,182, and the criticism this has received from epidemiologists in relation to the exploratory nature of epidemiology183,184,185 does not apply to external validation studies. For diagnostic and prognostic biomarker studies in particular, the registration of a study protocol with a predefined analysis plan has been recommended by several researchers153,154,186,187,188, provided that it precedes the onset of the study189. This would facilitate a more balanced evaluation of the proposed marker, identification and prevention of selective reporting, increased transparency, reduced proportion of false positive findings, mitigation of publication bias through identification of unpublished studies, and prevention of unnecessary duplication of research while facilitating collaboration between researchers and identification of research gaps. Consequently, widespread preregistration of detailed study protocols for deep learning systems might translate into more rapid identification of promising systems and thereby expedite progression of the research field. It would also communicate a study to peers without disclosing the findings and interpretations prior to editorial and peer review, thus providing some of the benefits of preprint archiving while allowing critical appraisal of the findings and interpretations before publication.

Amendments of clinical trial protocols are common but should be tracked and dated173. Whereas clinical trials often take years to conduct due to patient recruitment and follow-up, most external validations of deep learning systems use retrospective data, and the analysis part of the validation may be performed in a matter of days. Consequently, it should rarely be necessary to modify the study protocol describing the external validation of a deep learning system after initiating the validation. We therefore generally discourage protocol amendments, but if found necessary for a particular study, we recommend amendments to be included as postscripts to the study protocol, leaving the original protocol unaltered. Both the postscript and disseminations of the validation results should concretely specify what was changed as well as describe the motivation and rationale for the change.


Including much natural and artificial data variation when training rigorous deep learning systems appears pivotal, as analyses indicate its instrumental role in increasing the performance and generalizability of systems. Utilizing multiple sets of patients, samples and data acquisition procedures will diversify the training data, whereas augmentation techniques artificially enhance the variation further. The resulting systems may be capable of handling the diversity in routine medical practice and, in some cases, even generalize to completely new settings.

Going forwards, the medical validity of a deep learning system should be evaluated according to a preregistered study protocol specifying the primary analysis and using an external cohort representative of the intended medical setting and target population. This facilitates balanced performance evaluations by reducing selection bias and increasing transparency, and helps medical professionals distinguish rigorous, retrospective validation studies from studies that repeatedly evaluated the external cohort and might end up reporting severely biased performance estimates. Such preregistered study protocols would therefore assist in identifying deep learning systems that warrant prospective evaluations in randomized clinical trials and ultimately drive the development of systems that could transform current medical practice.


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The authors thank M. Seiergren for assembling all figures, T. S. Hveem for discussions, T. Ystanes, H. A. Inderhaug and B. M. Sannes for setting up and maintaining our computer network and computational infrastructure, and the authors of Inception-v3 for making their code freely available under an open source licence (Apache License, version 2.0). The authors of this Perspective acknowledge funding from the Research Council of Norway through its IKTPLUSS Lighthouse programme (project number 259204).

Author information




H.E.D and D.J.K initiated the project. All authors researched data for the article. A.K., O.-J.S. and K.L. evaluated the recent, presumably influential, deep learning studies in cancer diagnostics. S.D.R. executed the training, tuning and evaluation of Inception-v3 systems. A.K. drafted the manuscript, and all authors contributed to reviewing and editing the manuscript.

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Correspondence to Håvard E. Danielsen.

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Supplementary information


Area under the receiver operating characteristic curve

(AUC). A performance metric measuring the concordance between a dichotomous outcome and the ranking of subjects provided by a continuous or categorical marker. An AUC of 50% indicates random guessing and 100% indicates perfect prediction. For dichotomous markers, the AUC and balanced accuracy are equivalent.

Artificial neural networks

Mathematical functions mapping input data to output representations, structured as a directed graph of nodes and edges.

Balanced accuracy

A classification performance metric calculated by averaging the proportion of true predicted outcomes across all possible outcomes. For dichotomous outcomes, this reduces to the average between the sensitivity and the specificity.


The ability of a model class, for example a particular network architecture, to express complicated correlations between input data and target output. Model classes with high capacity have the potential to produce models that are able to map training data to target outputs with a high degree of accuracy, but are also more prone to overfitting.

Concordance index

(c-index). A performance metric measuring the concordance between a target outcome, usually defined by time to event data, and the ranking of subjects provided by a continuous or categorical marker. A c-index of 50% indicates random guessing and 100% indicates perfect prediction. For dichotomous outcomes, the c-index and the area under the receiver operating characteristic curve are equivalent.

Deep learning

A class of machine learning methods that make use of successively more abstract representations of the input data to perform a specific task, typically implemented using artificial neural networks. They also consist of an objective function that compares the final output with a target output as well as an optimization method that is used to optimize the objective function.

Deep learning models

Computational models obtained by training deep neural networks. Note that a single training of a neural network produces a sequence of models as each new optimization iteration produces a model slightly different from the previous one. A tuning data set may be used to select among these models.

Deep learning systems

Systems utilizing one or more deep learning models to make predictions. A system’s output may be a function of the outputs of the models, for example by averaging and thresholding the model outputs.

Development cohort

A cohort used for training and, sometimes, tuning and internal validation of a system.

External cohorts

Also known as independent cohorts, these differ non-randomly from the development cohort. In cancer diagnostics, the external cohorts will often contain patients suspected of having the same disease or disease attribute, at risk of developing the same event or suspected to respond to the same treatment as patients in the development cohort. However, external cohorts may be intentionally more different from the development cohort.

External validation

An evaluation of a system’s performance on an external cohort that did not influence the development of the system.


The ability of a system to perform similarly on subjects not included in training to on those included in the training. Poor generalizability can be caused by overfitting to the training data or by the lack of generally relevant features in the training data.


Utilizing noise or features in the training data that are not generally relevant for the prediction task but cause the system to perform better on the training sample.

Supervised machine learning

A methodology in which learning occurs by mimicking the mapping of input data to target output labels. By contrast, the input data are not associated with any output labels in unsupervised learning.


Although frequently used by the machine learning community to refer to an evaluation of a system’s performance, we use ‘test’ to refer to evaluations other than external validations, for example internal validations.


Optimization of model parameters based on data.


Informed selection of hyperparameter values (parameters not optimized during training) based on data. Examples include the network architecture, optimization method and threshold for a model’s continuous output. The nomenclature in machine learning is to use ‘validation’ instead of ‘tuning’.

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Kleppe, A., Skrede, OJ., De Raedt, S. et al. Designing deep learning studies in cancer diagnostics. Nat Rev Cancer 21, 199–211 (2021).

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