In recent years, the regulatory authorization of medical devices and digital health technologies based on big data and machine learning (ML) has accelerated [1]. ML solutions have the potential to transform clinical practice by automating diagnosis, enhancing clinical decision-making, improving patient monitoring, and personalizing treatment [2]. Diabetes care has been among the first clinical areas to adapt ML technologies [1,2].

Worldwide, pediatric diabetes mellitus (DM) is one of the most common chronic conditions among children, with growing incidence and increasingly complex presentation [3-6]. Type 1 DM (T1DM) is characterized by the lack of insulin secretion mainly due to autoimmune etiology, whereas type 2 DM (T2DM) is characterized by insulin resistance and metabolic syndrome associated with obesity [5]. Approximately 20% of children have both autoimmunity and insulin resistance [5]. A less common form, maturity-onset DM of the young, is attributed to a monogenic hereditary background [7,8]. Pediatric DM represents a difficult-to-treat population. Glucose targets frequently remain unmet in children and adolescents [9], and chronic complications, such as kidney disease, retinopathy, neuropathy, or hypertension, affect a significant proportion of patients by reaching young adulthood [10,11]. The life expectancy and quality of life of patients with pediatric DM may be reduced to a varying degree [5].

Within DM, pediatric DM has been leading the way to adopt digital technologies and intelligent devices [1,12]. Continuous glucose monitoring and automated insulin delivery systems are becoming an essential part of the management of children and adolescents with DM, with superior outcomes compared with alternative treatments [9,13]. Regulated smartphone apps for insulin dosing have become available for pediatric patients [14]. However, none of the currently available algorithms are optimal, and despite the use of advanced technology, many pediatric patients live under suboptimal glycemic control and are at risk of potentially serious long-term consequences [9,15]. In the quest for better disease characterization, prevention, and treatment of pediatric DM, ML has been increasingly applied from glucose sensors and artificial pancreas systems [16,17] to disease management apps (eg, mobile apps for food image–based carbohydrate counting or supporting self-management) [18,19] or risk prediction algorithms [20]. Although the comparison of novel algorithms has been challenging owing to methodological heterogeneity [9], artificial intelligence (AI) or ML algorithms have not been covered by DM technology guidelines [13,21,22]. To meet the needs of this challenging population, it is of utmost importance that algorithms are transparent and that their clinical value can be assessed.

Although expectations about the potential of technology to improve disease outcomes of pediatric DM have been rising [23,24], there has been growing concern about the transparency, replicability, biasedness, and overall validity of research in the field of AI and ML [25-30]. Indeed, examples of flawed or unfair predictions by algorithms and consequent legislative changes have sparked debate about the explainability, interpretability, and understandability of “black box” systems in ethical [31], philosophical [32,33], legal [34], social [35,36], computer [37], or medical sciences [38,39]. Although the concepts themselves remain vaguely defined or conflated [32], users in general and health care professionals in particular have sought explainable and interpretable ML models instead of predictions made by “black box” systems [40,41]. Although some ML models are “transparent” and others are “opaque” by nature, several post hoc techniques have been developed to make results interpretable, that is, to help medical professionals understand how and why machine decisions were made [40,41].

The outputs of ML models are probably more dependent on the input data than on the algorithm [42]. Therefore, the assessment of the fairness and accuracy of clinical ML studies should involve a thorough understanding of the processes of data production throughout the entire life cycle, from collection to annotation and processing [43]. Although technical aspects of data provenance may surpass the needs of clinicians, detailed reporting of the sources and production of data are indispensable for transparent and reproducible ML research and development [43].

We argue that high reporting quality standards are a prerequisite for the assessment and ultimately the achievement of methodological excellence in biomedical research. Although the association between incomplete reporting and biased treatment effects has been shown in clinical trials [44], evidence supports the positive effect of using checklists on reporting quality [45,46]. Despite the growing number and widespread adoption of reporting guidelines by leading journals over the past decades, deficient reporting of medical research studies remains a major concern, producing considerable waste [47].

Recognizing the limited usefulness of poorly reported studies in clinical practice, a plethora of reporting guidelines have been proposed for ML studies in medicine. Checklists have been developed for different study types (eg, observational studies, randomized trials, and health economic evaluations) and clinical areas aimed at standardizing the mandatory elements to be included in the study reports. These checklists are increasingly being used by scientific journal editors in medicine as mandatory elements for the submission of a manuscript [48]. Although targeting different apps and audiences, most reporting guidelines aim to ensure that results are reproducible, transparent, and, where appropriate, provide sufficient detail for inclusion in future evidence syntheses [26,30,48,49]. Hence, guidelines may contribute to the adoption of technologies with potential to benefit patients in real-world clinical settings.

Various apps and methods of ML in diabetes care have been systematically reviewed [50,51], including specific use cases such as the prediction of hypoglycemia [52] or complications [53,54], diagnosis [55,56], use in disease management [24,57], and smart devices [58]. However, to the best of our knowledge, the reporting quality of ML studies in pediatric DM has not been systematically reviewed.

By acknowledging the potential of ML methods in addressing the specific treatment challenges of pediatric DM, we aimed to systematically review the reporting quality of ML studies on pediatric DM using a structured reporting checklist. Specifically, we aimed to highlight areas with adequate or poor reporting quality and identify the indicators of reporting quality. Furthermore, we explored the association of reporting quality with expert judgments about the overall clinical usefulness of the reported results.

We considered the updated PRISMA (Preferred Reporting Item for Systematic Reviews and Meta-Analyses) 2020 statement when reporting the results of our study [59] (Multimedia Appendix 1). We searched the PubMed and Web of Science databases for the 5-year period from January 1, 2016, to December 31, 2020, using search syntaxes that combined the terms ML, children, and DM. For ML, we constructed a comprehensive search filter using the Medical Subject Headings (MeSH) terms of ML and AI [60,61]. We extended the search phrase with a list of terms from the caret package [62]. Given the rapidly expanding list and specialized use of methods, terms were added based on expert judgment. For studies on children, we adapted the Cochrane child search filter [63] by removing terms related to infants who were outside the scope of our study. In addition to the MeSH terms, the DM filter also included hyperglycemia, hypoglycemia, ketoacidosis, and insulin resistance. The detailed syntaxes and dates of the search in the PubMed and Web of Science databases are provided in Multimedia Appendix 2 and Multimedia Appendix 3, respectively.

Original research reports published from 2016 to 2020 were eligible if ML methods were applied to analyze patient data on a population of children aged 2 to 18 years with DM of any subtype. As the primary research goal concerned the reporting quality of the applied ML methods, outcomes and interventions were not specified among the eligibility criteria. We restricted our review to a 5-year window to keep track of recent advances and maintain a feasible range. We included studies if DM or its complications (eg, retinopathy) were the primary diagnosis or DM was a study subpopulation (eg, population screening studies). If the relevant age group was covered, patients aged up to 25 years were accepted. We also included studies involving broader age groups if the results were reported separately for children. Both in vivo and in silico pediatric patients were allowed. No language restrictions were applied.

All records were independently screened by 12 pairs of reviewers formed by 6 authors. An extensive list of ML methods was provided to aid in record screening. Differences were resolved by consensus. Records were excluded if ineligibility could be clearly stated and retained for full-text screening in case of uncertainty or insufficient information.

The full-text reports were independently screened by 12 pairs of reviewers. All eligibility criteria were recorded and had to be reconciled in case of disagreement. Eligibility for the ML criterion was as follows: (1) either a typical ML method was specified (eg, bagging, boosting, bootstrap aggregated models, decision tree, deep belief network, denoising autoencoder, ensemble methods, genetic programming, learning, long short-term memory, model tree, neural network, neuro-fuzzy, random forest, random tree, and support vector) or (2) the data analysis algorithm involved the ML workflow of training, validation, and testing of results using any algorithm including traditional regression methods. In case of uncertainty, a third reviewer (AM) with technical expertise in ML methods made the decision. The third reviewer was omitted only if reviewers mutually agreed on the presence of criterion 1 or the absence of both criterion 1 and 2. Interrater agreement of reviewers was monitored during the screening of records and selection full-text reports via absolute agreement and Cohen κ.

In addition to the assessment of reporting quality, the first author, publication year, Scimago subject category of the publication (engineering and medicine) [65], title, main goal, applied ML method, input data, characteristics of the pediatric training and testing samples, and key findings of the included papers were extracted by a single reviewer (ZZ). Quantitative characteristics were extracted (eg, sample size), and inductive coding was applied to group studies into categories according to their goals, features of the training and test samples, and input data.

We provided qualitative summaries of the answers to the MI-CLAIM by study and item. For each study, we denoted the count of “yes,” “no,” and “unsure” answers as well as the categories for data type (item 2.5) and reproducibility (item 6.1) as the MI-CLAIM profile of a study. For quantitative analysis, reproducibility (item 6.1) was dichotomized as “any sharing” (tiers 1-3) and “no sharing” (tier 4). In addition, the count of “yes” ratings for each study was referred to as reporting quality.

We assessed the association between reporting quality and continuous, dichotomous, and polytomous study characteristics using Pearson correlation, 2-sample t test, and one-way ANOVA, respectively. The normality of the distribution of reporting quality was tested using the Shapiro-Wilk test. The association between study characteristics and reporting quality (ie, “yes” ratings) was assessed via cross-tabulation and the Fisher exact test for each MI-CLAIM item.

Furthermore, we evaluated the correlation between reporting quality and the overall expert assessment of clinical impact. The association between reproducibility (item 6.1) and overall expert assessment of replicability was tested using a 2-sample t test.

The searches in PubMed and Web of Science databases yielded 717 and 336 records, respectively. After removing 9 duplicates, 1043 publication records were screened, 298 full-text reports were checked for eligibility, and 28 reports were eligible for our review. Research activity increased rapidly over time: 64% (18/28) of papers were published during the last 2 years, and 43% (12/28) were published in 2020 alone. (For web-based papers, the year of publication was subsequently updated in some cases). We assessed 21 reports using MI-CLAIM. Due to initial differences between reviewers, 20.4% (213/1043) of the records were reconciled. The absolute agreement and Cohen κ between reviewers’ initial judgments were 79.6% (range 63%-94%) and 0.47 (range 0.15 to 0.83), respectively. In the screening of full-text reports, 12 could not be retrieved due to lack of institutional access (Multimedia Appendix 4), 286 were assessed, 24.1% (69/286) were reconciled between reviewers, and in 13.6% (39/286) of the cases, a third reviewer was invited after the reviewers’ discussion to decide on the ML criterion. Altogether, the absolute agreement and κ of reviewers’ initial judgments regarding full-text selection were 67% (range 20%-85%) and 0.30 (range 0.06-0.30), respectively (Multimedia Appendix 5). Details of the search, screening, and inclusion are provided in the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) flowchart (Figure 1).

The characteristics of the 28 included studies are summarized in Table 1.

Most studies (n=6) focused on the discovery of etiologic or prognostic biomarkers of T1DM [77,80,81,85,88,89], followed by studies aiming to predict hypoglycemia using noninvasive methods such as ECG or EEG signals, breath volatile organic compounds (n=5) [21,67,69,70,76], insulin bolus calculators for closed-loop glucose control (n=5) [66,82-84,90], accurate prediction of glucose levels or hypoglycemia from continuous glucose monitor (CGM) data (n=4) [72,73,78,79], etiologic or risk factors for insulin resistance or T2DM (n=4) [71,74,75,86], and other goals such as long-term cardiovascular risk stratification [68], accurate carbohydrate counting via a smartphone app [18], prediction of cystic fibrosis–related DM from CGM signal [87], and the economic evaluation of diabetic retinopathy screening via AI versus standard care [91].

The characteristics of the training sample (including the validation data set) were not reported in 3 studies [18,90,91]. Of the 25 studies reporting details, in 18 (72%), the training sample involved human patients, in 6 (24%) only in silico patients [66,72,73,82-84], and there were both human and in silico patients in one study [78]. Of the 9 studies focusing on bolus calculation or glucose prediction from CGM data, only 2 (22%) had human patients in the training sample [78,79], 6 (67%) had only in silico patients [66,72,73,82-84], and the training sample was not characterized in one study [90]. The size of the training sample ranged from 561 [68] to 5 [76]. Of the 25 studies reporting details, only 10 (48%) had training samples with more than 100 patients [68,71,74,77,78,81,85-88], whereas 9 (36%) involved 10 or fewer patients [67,69,70,72,73,76,82-84]. Etiologic or prognostic studies for T1DM [77,80,81,85,88,89] and T2DM [71,74,75,86] featured the largest training samples ranging between 56 and 418 and 45 and 373, respectively. However, of the 14 studies focusing on insulin bolus calculators, or glucose or hypoglycemia prediction, only 4 (29%) [21,66,78,79] involved more than 10 patients in the training sample, with 141 being the largest sample size [78].

The test sample was characterized in 21 studies that involved a full ML workflow. Testing was performed on the same patients as the training in 12 (57%) studies, involving time-split in 8 studies using CGM data [66,72,73,76,78,82-84] and cross-validation in 4 studies [21,68,77,80]. In 5 (24%) studies, the test sample involved randomly selected patients from the same center as the training sample [67,69-71,79]; in 2 (10%) studies, patients from one or more external centers [75,81]; and in 2 (10%) studies randomly selected patients from multicenter studies [74,85]. The test sample included 10 or fewer patients in 10 (48%) studies [67,69,70,72,73,75,76,82-84], and only 4 (19%) studies featured test samples involving more than 100 patients [68,74,77,78]. The sample sizes of the external test samples ranged between 10 and 186 [74,75,81,85].

In the 28 included studies, we identified a plethora of ML methods that sometimes overlapped with the techniques used for feature engineering, dimension reduction, or other steps of the analysis. Altogether, from the 87 proposed or comparator methods used, we identified 61 different techniques, with random forest (RF) mentioned in 8 studies [74,77-80,86,88,89], followed by feed forward neural network in 5 studies [69,70,72,73,81], logistic regression in 4 [74,77,79,80], and multiple regression (MR) [67,69,70] and naive Bayes in to 3-3 studies [77,80]. There were 48 methods mentioned in only one paper, and 2 papers did not specify the ML algorithm [90,91].

The reporting quality via MI-CLAIM was assessed in 21 studies that followed the ML workflow. The characteristics of the assessed studies are summarized in Multimedia Appendix 6 [21,66-85]. The MI-CLAIM profiles for each study are shown in Figure 2 [21,66-85]. The assessment details of the included studies are provided in Multimedia Appendix 7 [21,66-85]. To support our “yes” ratings, the summaries of reported items for each study by the domains of MI-CLAIM are provided in Multimedia Appendices 8-11 [21,66-85].

For the 17 binary items, the number of “yes” ratings ranged between 4 and 12 (mean: 7.43), the “unsure” ratings ranged between 0 and 7 (mean 3.62), and the “no” ratings ranged between 2 and 12 (mean 6.95). One study provided a link to the applied unique ML model framework [85], without disclosing the specific code applied in the analysis. We rated reproducibility (item 6.1) for this study as “unsure” and dichotomized it as “any sharing.” The distribution of reporting quality was normal (Shapiro-Wilk test; P=.11). Reporting quality correlated positively with the year of publication, showing an improvement over time (r=0.50; P=.02). The reporting quality did not differ between studies using structured [21,67,68,70-74,76,77,79,80,83-85] or unstructured data [66,69,70,75,78,81,82] (t₁₉=0.35; P=.73), or whether the input data were time series [66,69,70,72,73,78,79,82-84], omics [18,21,74,77,80,81,85], or other [68,71,75,76] (ANOVA F_2,18=2.21; P=.14), in silico [66,72,73,82-84] or human subjects were involved [21,67-71,74-81,85] (t₁₉=1.23; P=.24). However, it differed between studies with different research goals (ANOVA, F_5,15=4.59; P=.01). Compared with the mean, prognostic biomarker studies in T1DM and risk factor studies of T2DM had significantly higher reporting quality by 2.02 (P=.04) and 2.85 (P=.01) “yes” ratings, respectively, whereas noninvasive hypoglycemia detection studies had fewer “yes” ratings by 2.69 (P=.006). Furthermore, higher reporting quality was observed in studies sharing any code of the ML pipeline [71,75,85] (t₁₉=3.48; P=.003) and in studies published in medical journals [21,66,68,71,74,75,78-81,84,85] (t₁₉=3.24; P=.004). Reporting quality correlated moderately with the overall expert assessment of clinical impact without significant association (r=0.40; P=.07).

Figure 3 shows an assessment of reporting quality by the MI-CLAIM items [21,66-85].

This systematic review provides insights into reporting quality and, hence, the potential clinical impact of studies applying ML methods in pediatric DM populations. We applied the MI-CLAIM checklist to assess the reporting quality of 21 studies that followed the ML workflow of model training, validation, and testing. In these studies, reporting quality was generally low, with an improving trend over time. The MI-CLAIM items on research questions and data characterization were reported adequately most often, whereas the items on patient characteristics and model examination were reported adequately least often. The representativeness of the training and test cohorts to real-world settings and the adequacy of model performance evaluation were the most difficult to judge. On average, we found adequate reporting for less than half of the MI-CLAIM items, with considerable differences between studies with different research foci. Medical papers had higher reporting quality compared with articles published in engineering journals, mainly because of more elaborate reporting in the model examination domain. The number of MI-CLAIM items with a “yes” rating showed a moderate correlation with the overall assessment of the clinical impact by independent medical experts. We found no association between the reproducibility ratings on MI-CLAIM and independent experts’ assessments of the technical replicability of studies.

When writing this paper, MI-CLAIM was used in a single review, focusing on ML in dental and orofacial pain management, in which nearly all included papers were rated with “yes” in 13 or more out of the 15 assessed items [92]. Our study showed a less favorable picture with all studies having 12 or less “yes” ratings and two-thirds of studies having 7 or less “yes” ratings out of 17 items. Our findings corroborate the results of previous studies, raising concerns regarding the reporting quality of ML studies [25,27,29].

Considering the globally increasing burden and serious consequences of pediatric DM [3] and the rapid growth of ML literature over the past years [48], we found few eligible studies, usually involving small patient populations. Of the 28 eligible studies, the training sample involved more than 100 patients in only 10 cases. In terms of research aims, applied methods, and data types, the studies were diverse.

According to our experience, compared with highly standardized medical papers, such as randomized clinical studies [93], systematic reviews [94], or economic evaluations [95], the reading and interpretation of the involved ML papers was challenging and time-consuming. The focus of MI-CLAIM on the clinical utility of ML modeling may explain the higher reporting quality of medical papers than those published in engineering journals. Still, the general reporting pattern reflected a “data-driven” mindset: after stating the clinical problem and research question, data-related items were reported most thoroughly. However, important details for clinicians, such as the detailed description of patient cohorts, the state-of-the-art clinical solution, and the clinical utility of the proposed models and model examination for valid, unbiased, and robust results were often the weak points of reporting.

We found an association between reporting quality and research goals. Studies with a strong clinical focus, such as those seeking prognostic biomarkers in T1DM and risk factors in T2DM, had higher reporting quality than the more technically oriented studies aimed at detecting hypoglycemia from CGM data or noninvasive methods or developing insulin bolus calculator algorithms. However, some of the reported differences were clearly attributable to the individual styles of the research teams. While reporting quality of the same teams, such as Webb-Robertson et al [77,80,85], Zhu et al [82-84], Bois et al [72,73], or Ling et al [67,69,70] fell in the same range, the number of “yes” ratings differed up to 6 items between different author teams in similar studies focusing on hypoglycemia prediction or the discovery of prognostic markers for T1DM.

Although MI-CLAIM was developed as a general reporting checklist, not as a measurement tool, our attempt to quantify reporting quality provided several learnings. We observed that the applicable ratings in some items depended on the underlying methods. For example, the independence of the training and test data could not be demonstrated in studies aimed at developing individualized glucose control algorithms. In contrast, the use of transparent models and a thorough examination of feature importance are hallmarks of prognostic marker studies, yielding naturally high scores in the model examination domain. Specific research questions, methods, or data types gave rise to specialized ML reporting guidelines for certain clinical fields or research designs [30,48]. Although MI-CLAIM provides a strong strategic framework for the evaluation of a broad range of ML applications, in our opinion, the evaluation of the validity and potential biases of ML studies in specific clinical use cases of pediatric DM, such as insulin bolus calculation or hypoglycemia detection from various physiological signals, would require more specific technical guidance, preferably from the medical profession, who provides the data and ultimately uses the results for clinical decision-making.

Some MI-CLAIM items received a high proportion of “unsure” ratings from our team. For example, item 1.4 suggests that the representativeness of training and test cohorts in real-world clinical settings should be demonstrated. Despite many studies reporting the parameter variability of T1DM simulators or the recruitment methods and characteristics of patient samples from diabetes clinics, we were unsure about what the established criteria were for representative cohorts of pediatric T1DM or T2DM. In addition, items 4.1 and 4.2 frequently received “unsure” ratings, which require that the primary evaluation metrics for model performance and clinical utility are clearly stated and justified. Although some authors “cherry picked” among multiple performance metrics to declare the superiority of the proposed model, in many cases, the assessment of adequate reporting was more challenging. For example, some studies applied the Clarke Error Grid Analysis [96] to evaluate the clinical accuracy of glucose predictions, reporting results in all 6 regions, but did not specify the primary region of interest (eg, potentially hazardous prediction errors). Other studies reported both sensitivity and specificity for hypoglycemia predictions without specifying a single measure. Furthermore, many studies have reported meaningful measures for the evaluation of model performance and clinical utility, without specifying their purpose. Examples include specificity and sensitivity, or the imaging study of Langner et al [75], which reported 3 metrics: the Dice score [97] and absolute and relative estimation error of adipose tissue volume. Although the metrics were adequate for both technical and clinical evaluation of results, owing to the lack of a single primary evaluation metric, the MI-CLAIM items could not be rated with unanimous “yes.” Furthermore, we found an overlap within the model examination domain, where the same piece of information satisfied multiple items, especially when the model examination involved performance testing in special patient populations.

Finally, we must note the diversity of methods and nomenclature used from data processing to feature selection, prediction, or evaluation of results. We found nearly 2 unique ML methods per paper, which makes the systematic search and evidence synthesis of ML challenging. While the term “machine learning” yielded 42,840 hits, our extended search term using specific methods provided 235,042 hits over our study’s search period in PubMed (Multimedia Appendices 2 and 11). While keeping track of the novel methods in ML is nearly impossible, the omission of specific terms carries the risk of incomplete search results for evidence synthesis. Furthermore, due to the specific methodological and reporting concerns about ML in medicine, we propose that the “machine learning study” label should be consistently used in the titles of medical studies, whose primary results arise from the typical data-driven ML workflow. This term has been used in the title or abstract of only 101 papers in PubMed in the same search period and could serve as unique identifier of clinical research using ML methods (Multimedia Appendix 12), benefiting future information retrieval and evidence synthesis similarly to the “randomized controlled trial” label.

A limitation of our study was that the literature search was closed in early 2021; therefore, recent publications potentially eligible for our review were not covered. In addition, given the plethora of ML methods, although the detailed list was included in the search syntax, some studies may have been missed during the search phase of our study. However, we believe that the key observations and conclusions of our review remain unaffected. In addition, we did not assess studies using MI-CLAIM, which reported ML results in pediatric DM without applying the ML workflow of model training, validation, and testing. Specific ML reporting guidelines exist [30,48] for clinical pilot studies [18], randomized controlled studies [90], and economic evaluations [91]. Despite the use of MI-CLAIM for a breadth of study types, we considered that MI-CLAIM was not applicable for a comparable assessment of those studies that omitted the steps of model validation and testing [86-89] with those that followed the full ML workflow.

Furthermore, despite the involvement of both medical experts and computer scientists in our research team, we observed high rates of disagreement between reviewers, and our consolidated ratings were “unsure” in over 20% of the assessed items. Although MI-CLAIM items were elaborated in group trainings, due to subjective judgments, some inconsistencies may have remained in our ratings. In particular, our judgments were unsure whether the representativeness of the training and test samples in real-world clinical settings was adequately demonstrated or if the selection and justification of primary model performance evaluation metrics were adequately justified. The specification of adequate sample characteristics and model performance evaluation criteria for clinical decision-making in pediatric DM and other disease areas remains an important area for future research.

The reporting quality of ML studies in the pediatric population with DM was generally low. Important details for clinicians, such as the detailed description of patient cohorts, the state-of-the-art clinical solution, the clinical utility of the proposed models, and model examination for valid, unbiased, and robust results, were often the weak points of reporting. To allow the assessment of their clinical utility, it is of utmost importance that the reporting standards of ML studies evolve and algorithms for this challenging population become more transparent and replicable. MI-CLAIM provided a strong strategic framework for good reporting practices, which could be further supported by disease-specific technical guidance regarding what constitutes an adequate level of detail to inform clinical decision-making. Higher reporting quality standards may indirectly advance science and facilitate the uptake of technologies that have the potential to benefit children with DM.