Prognostic models for predicting intensive care unit admission or mortality in critically ill adults not yet been admitted to the intensive care unit

Objectives

This is a protocol for a Cochrane Review (prognosis). The objectives are as follows:

To determine whether prognostic models can be used for predicting the occurrence of ICU admission and mortality within the index hospital admission, and post‐discharge survival at reported follow‐up time points, up to one year, in critically ill adults not yet admitted to the ICU.

The objective in PICOTS format is as follows.

• Population: critically ill adults not yet admitted to the ICU

• Index prognostic model: available prognostic models with or without external validation

• Comparator: not applicable

• Outcomes: ICU admission, ICU and hospital mortality, and post‐discharge survival

• Timing: for ICU admission or transfer, ICU mortality, and hospital mortality outcomes, the timing will be in hospital. For post‐discharge survival, the timing will be up to 28 days, 1 to 3 months, 6 months, and 1 year after hospital discharge.

• Setting: acute hospital wards and emergency care departments

Background

Description of the health condition and context

In 2021, the worldwide average of intensive care unit (ICU) beds was 8.73 per 100,000 people across 87 countries, with patients staying between 5 and 18.5 days [1, 2]. The length of ICU stay is commonly affected by the severity of illness of the patient, and can be influenced by care management timeliness. Unplanned or delayed ICU admissions are concerning, and impact about 9% to 40% of patients [3, 4]. Nearly 90% of such admissions result from new or worsening conditions and delayed recognition of clinical deterioration [5, 6], thus increasing costs, the healthcare providers' workload, and the risk of serious adverse events (such as cardiac arrest) and death [7, 8]. Predicting admission to ICU and mortality by using prognostic models, especially in patients not yet admitted to the ICU, may be key to promoting individualised and patient‐centered care in potentially critically ill patients.

Description of the prognostic model

A prognostic model is a mathematical equation that integrates multiple predictors to provide a reliable estimate of an individual's risk of experiencing a specific outcome [9, 10]. These models may incorporate a range of predictive factors, such as clinical and physiological parameters, and generate a numerical estimate of the risk of outcomes including mortality, prolonged hospitalisation, and adverse events (e.g. cardiac arrest) [11, 12, 13, 14]. To date, no prognostic model has been established as a gold standard for predicting ICU admission or mortality outside the ICU. This may be partly explained by the heterogeneity of these patient populations assessed in different clinical settings, such as hospital emergency departments and acute hospital wards, with varying severity of illness, comorbidities, and timing of assessment. Heterogeneity may also arise from differences in healthcare resources, monitoring capacity, escalation pathways, ICU admission thresholds, and geo‐economic contexts. In addition, the prediction of ICU admission is particularly challenging because this outcome is partly resource‐dependent. Even when a model accurately identifies patients with greater clinical severity or higher risk, ICU admission may not occur if ICU beds are unavailable or if local admission thresholds differ. Although most models have undergone extensive validation, primarily in high‐income countries, their predictive performance varies [15, 16, 17, 18, 19, 20, 21]. Also, the range of outcomes assessed in published systematic reviews remains limited [22, 23, 24].

Why it is important to do this review

Several systematic reviews have evaluated prognostic models for patients cared outside the ICU. However, they considered a limited set of outcomes, such as mortality, length of stay, and models’ accuracy for predicting the outcomes. In addition, there were methodological limitations, such as limited search strategy, absence of tools to assess risk of bias, and limited inclusion of different prognostic models [14, 22, 25, 26, 27, 28, 29, 30]. A comprehensive search strategy is needed to identify methodologically sound models for predicting admission to ICU and mortality in critically ill adults. This evaluation should consider various settings and patient profiles to improve equity, personalisation, and accuracy in decision‐making. This review is highly relevant to physicians who must choose whether to request an ICU bed, a change to the patient care plan, or recommend surveillance. It is also relevant to conduct future research on external validation of existing prognostic models, potential impact studies of such models, and research on developing new prognostic models.

Objectives

To determine whether prognostic models can be used for predicting the occurrence of ICU admission and mortality within the index hospital admission, and post‐discharge survival at reported follow‐up time points, up to one year, in critically ill adults not yet admitted to the ICU.

The objective in PICOTS format is as follows.

• Population: critically ill adults not yet admitted to the ICU

• Index prognostic model: available prognostic models with or without external validation

• Comparator: not applicable

• Outcomes: ICU admission, ICU and hospital mortality, and post‐discharge survival

• Timing: for ICU admission or transfer, ICU mortality, and hospital mortality outcomes, the timing will be in hospital. For post‐discharge survival, the timing will be up to 28 days, 1 to 3 months, 6 months, and 1 year after hospital discharge.

• Setting: acute hospital wards and emergency care departments

Methods

We will follow the Transparent Reporting of a Multivariable Prediction Model for Individual Prognosis or Diagnosis (TRIPOD) Systematic Reviews and Meta Analysis (TRIPOD‐SRMA) guidelines for reporting the review [31].

Criteria for considering studies for this review

Types of studies

We will include retrospective and prospective cohort studies, prognostic studies based on registries, and cohort data from randomised controlled trials (RCTs). The studies will be included regardless of their publication status or language. We will exclude studies published only as abstracts. In hospitals with limited resources, such as those in low‐ and middle‐income countries (LMICs), patients with ICU status sometimes continue in emergency rooms due to the lack of a bed in an ICU. Therefore, we will not exclude any studies based on the prognostic timing or time horizon to which the prognostic models apply.

Types of participants

• Adults aged 18 years or older assessed in an emergency department or acute hospital ward, provided that the study defines a clearly identifiable and pre‐specified eligible population

• Patients who have not been admitted to an ICU at the time of prediction

If we identify studies with mixed populations in which only a subset of participants is eligible, we will include them only if the study authors report separate data for eligible participants. If such disaggregated data are unavailable, we will contact the study authors when over 80% of participants meet our inclusion criteria to obtain the necessary information. We will exclude pregnant women, surgical patients, individuals with neurological conditions, trauma populations, and patients receiving exclusive palliative care or with do‐not‐resuscitate orders. These groups follow distinct physiological trajectories and clinical pathways that require dedicated prognostic models, and would introduce substantial heterogeneity unrelated to the focus of this prognostic review.

Types of prognostic models

We intend to identify all prognostic models available and judge their performance. We will consider model development studies, validation studies, and studies that adapted an existing model. A study will be considered to report a prognostic model if the aims, results, or discussion focus on the model as a whole, rather than solely on individual predictors or methodological aspects. Studies will not be restricted by the modelling approach used, including both traditional statistical methods and machine learning techniques. We will exclude studies that evaluated models based only on single prognostic factors, as well as studies that report only adjusted predictor effects without assessing or discussing the predictive performance of the model (e.g. discrimination, calibration, or classification). We will also exclude models that focus on predicting either beneficial or harmful treatment responses.

Outcome measures

Critical outcomes

We will include the following critical outcomes.

• Admission or transfer to an ICU bed

• ICU mortality (number of unexpected deaths in ICU (i.e. death without a "not for resuscitation" order)

• Hospital mortality

Important outcomes

• Post‐discharge survival (survival after discharge from intensive care)

For post‐discharge survival, we will extract the prediction horizon reported for each model. Where possible, post‐discharge survival will be grouped into clinically meaningful time points, such as up to 28 days, 1 to 3 months, 6 months, and 1 year after hospital discharge. If a study reports an outcome more than once within the same time period, we will use the latest time point within that category. If needed, we will select the time point that best aligns with other studies to enable comparisons for each outcome.

Electronic searches

We will base the refined search strategy on previous studies [32, 33]. All search strategies are presented in Supplementary material 1.

We will conduct a literature search to identify all published and unpublished studies. No language restrictions will be applied. We will translate non‐English language papers and fully assess them for potential inclusion in the review, as necessary. In addition, we will use reference management software to remove duplicates.

We will search for the following sources.

• Cochrane Central Register of Controlled Trials (CENTRAL) (1996 to date of search)

• MEDLINE via PubMed (1946 to date of search)

• Embase via Elsevier (1947 to date of search)

• World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) (https://trialsearch.who.int/Default.aspx)

Searching other resources

We will screen the reference lists of all included studies and relevant systematic reviews. Where possible and necessary, we will contact the authors of all the included studies for further information on unpublished or ongoing studies. Additionally, we will conduct grey literature searches through OpenGrey and Google Scholar.

As part of our search strategy, we will actively monitor for any post‐publication amendments concerning included or eligible studies. Specifically, we will undertake the following tasks.

• Check for expressions of concern, errata, corrigenda, and retractions by consulting relevant databases such as Retraction Watch, PubMed, and CrossMark

• Review publisher websites and journal pages for notices related to included studies

• Use automated alerts and database updates to identify any changes occurring after publication

We will document and report all identified amendments within the review. Furthermore, as recommended in Chapter 5 of the Cochrane Handbook for Systematic Reviews of Interventions, we will assess the potential impact of such changes on the validity and conclusions of the review [34].

Data collection and analysis

Selection of studies

We will use Covidence software to identify and remove duplicated records [35]. Two review authors (AGSV and RKN) will independently screen all titles and abstracts. The full‐text study reports for all references coded as 'include' by either review author will be retrieved. The same two review authors will independently screen the full‐text studies, and will record the reasons for exclusion of studies after full‐text assessment. Disagreements will be resolved through discussion or, if required, by consulting one of the clinical authors (GSS). We will collate multiple reports of the same study so that each study, rather than each report, is the unit of interest in the review. We will also include any information we can obtain about ongoing studies. We will record the selection process in sufficient detail to complete a PRISMA flow diagram.

Data extraction and management

We will develop a dedicated data extraction form based on the Checklist for Critical Appraisal and Data Extraction for Systematic Reviews of Prediction Modelling Studies (CHARMS) [36, 37], adapted for prognostic models.

Before beginning the extraction process, two review authors (AGSV and AAAG) will test the data extraction form using a representative sample of the studies included in the review. Following this pilot test, we will adjust the data extraction form as necessary and develop comprehensive coding instructions. If major changes are needed after the first test, we will repeat the pilot test using a new set of studies before starting data extraction. If the data extraction form or coding instructions require modifications after they have been tested, we will return to reports that have already undergone data extraction, as necessary.

For every included study, we will extract all prognostic models relevant to our study objectives, and for each included prognostic model, we will extract the following information.

• Baseline characteristics of study participants, including age, gender distribution, admission cause, symptom durations, study setting of prognostic model, and first admission or readmission after hospital discharge

• Study characteristics, including study design, number of participants, model development, methods for validation or refinement, or both, timeframe, inclusion and exclusion criteria, predictor definitions and effect sizes, outcome definitions, details regarding the model evaluation (e.g. bias correction techniques), handling of missing data, and details relevant to the risk of bias assessment

• Model performance, including discriminatory ability and calibration, are crucial information for assessing the clinical applicability of the model, including its usability, acceptability, and complexity

We will contact study authors to request additional information as appropriate. Any disagreements will be resolved through consensus. One review author (AAAG) will transfer the data regarding 'Characteristics of included studies' and 'Characteristics of excluded studies' from the data collection form to Review Manager (RevMan) software [38]. We will double‐check that the data is entered correctly by comparing the study reports with the data presented in the systematic review.

Risk of bias assessment in included studies

We will use the Prediction Model for Risk of Bias Assessment tool Artificial Intelligence (PROBAST+AI) to assess the risk of bias of the included studies [39]. The assessment process involves the following four steps.

• Specifying the systematic review question(s)

• Classifying the type of prediction model evaluation

• Assessing the risk of bias and applicability

• Making an overall judgment about the risk of bias and applicability

Using PROBAST+AI, we will assess risk of bias and applicability across four domains, Table 1, 34 signalling questions (16 for model development, 18 for model evaluation), and six applicability items (three for model development and three for model evaluation). Judgement of the risk of bias will be facilitated by signalling questions, which can be answered with ‘yes’, ‘probably yes’, ‘probably no’, ‘no’, or ‘no information’. Two review authors (CGM and AGSV) will independently assess risk of bias and applicability. Each domain will be judged as either ‘low’, ‘unclear’, or ‘high’ risk of bias. We will make an overall risk of bias judgement across domains.

1. PROBAST+AI: Assessment of risk of bias and applicability.

Participants and data sources	Predictors	Outcomes	Analyses
Model development
Signalling questionsa:
1.1 Were appropriate data sources used?	2.1 Were predictors defined and assessed in a similar way for all participants?	3.1 Were outcomes defined and assessed appropriately?	4.1 Was there evidence that the sample size was reasonable?
1.2 Was an appropriate study design used?	2.2 Was any preprocessing of predictors similar for all participants?	3.2 Were outcomes defined and assessed in a similar way for all participants?	4.2 Were continuous and categorical predictors handled appropriately?
1.3 Did the inclusions and exclusions of study participants result in a representative dataset?	2.3 Were predictor assessments made without knowledge of outcome data?	3.3 Were outcome assessments made without use or knowledge of predictor data?	4.3 Were participants with missing or censored data handled appropriately in the analysis?
	2.4 Were the predictors included in the model available at the time the model was intended to be used?	3.4 Was the time interval between predictor assessment and outcome assessment appropriate?	4.4 If methods to address class imbalance were used, was the model or the model predictions recalibrated?
			4.5 Were methods used to address potential model overfitting?
Qualityb:
Concern regarding quality of selection of participants and data sources	Concern regarding the quality of the predictors or their assessment	Concern regarding quality of the outcome or its determination	Concern regarding quality of the analysis
Applicabilityb:
Concern that the data of the included participants do not match the review question or the assessor’s intended use of the prediction model	Concern that the definition, preprocessing, assessment, or timing of assessment of the predictors in the model do not match the review question or the assessor’s intended use	Concern that the outcome, its definition, assessment, or timing of assessment do not match the review question or the assessor’s intended use
Model evaluation
Signalling questionsa:
1.1 Were appropriate data sources used?	2.1 Were predictors defined and assessed in a similar way for all participants?	3.1 Were outcomes defined and assessed appropriately?	4.1 Was model evaluation based on only apparent performance avoided?
1.2 Was an appropriate study design used?	2.2 Was any preprocessing of predictors similar for all participants?	3.2 Were outcomes defined and assessed in a similar way for all participants?	4.2 Was there evidence that the sample size was reasonable?
1.3 Did the inclusions and exclusions of study participants result in a representative dataset?	2.3 Were predictor assessments made without knowledge of outcome data?	3.3 Were outcome assessments made without use or knowledge of predictor data?	4.3 Were participants with missing or censored data handled appropriately in the analysis?
—	2.4 Were the predictors included in the model available at the time the model was intended to be used?	3.4 Was the time interval between predictor assessment and outcome assessment appropriate?	4.4 If methods to address class imbalance were used, was the evaluation done in a dataset without correction for imbalance?
—	—	—	4.5 If data splitting was done to create training and test datasets, was there evidence that data leakage was avoided?
—	—	—	4.6 If resampling methods were used to evaluate model performance, were all model development steps replicated in the resampling process?
—	—	—	4.7 Was the predictive performance of the model evaluated appropriately—for example, calibration, discrimination, and net benefit?
Risk of biasb:
Risk of bias introduced by the selection of participants and data sources	Risk of bias introduced by the predictors or their assessment	Risk of bias introduced by the outcome or its determination	Risk of bias introduced by the analysis
Applicabilityb:
Concern that the data of the included participants do not match the review question or the assessor’s intended use of the prediction model	Concern that the definition, preprocessing, assessment, or timing of assessment of the predictors in the model do not match the review question or the assessor’s intended use	Concern that the outcome, its definition, assessment, or timing of assessment do not match the review question or the assessor’s intended use	—

^aAnswered as yes, probably yes, probably no, no, no information, or not applicable.
^bRated as either low, high, or unclear.

Studies assessed as low risk of bias across all domains will be considered to have an overall low risk of bias. We will determine the overall risk of bias as ‘high’ if any domain is high, ‘uncertain’ if any domain is uncertain, and all others as ‘low’. To ensure consistent application, two review authors (CGM and AGSV) will pilot the tool, discuss any discrepancies in its use, and establish agreed‐upon guidelines for its application. The two review authors will resolve any discrepancies through discussion; if consensus cannot be reached, a third review author will adjudicate. When a study involves the development of multiple models or includes both the development and external validation of a model, we will assess the quality of each model and external validation separately.

If the information is insufficient to make a judgment, we will contact the corresponding study authors by email to request additional information so that we can make robust assessments of the risk of bias.

Measures of predictive performance

Performance measures obtained from the included prognostic models will encompass discriminatory ability (C‐statistic, area under the curve (AUC)) and calibration (calibration slope, ratio of observed (O) to expected (E) events (O:E ratio), calibration plots). We will assess the predictive performance of models according to the type of outcome. For time‐to‐event outcomes, we will extract measures of discrimination and calibration (e.g. calibration slope). For dichotomous outcomes, we will extract corresponding metrics, such as AUC and calibration performance.

Dealing with missing data

We will contact corresponding study authors via email to request additional or updated information that is unavailable in the published articles. If performance measures and their precision measures are missing, we will calculate them where feasible [36]. We will descriptively report the extent of missing data for study characteristics and cohort background characteristics in text, tables, or both. In addition, we will explore the impact of missing data in a sensitivity analysis.

Reporting bias assessment

We will identify and outline significant shortcomings in the reporting of studies, based on the criteria set by the TRIPOD guidelines [40]. In addition, if we identify a prognostic model with 10 or more unique external validations, we will perform a test for funnel plot asymmetry using the R package ‘metamisc’ and produce contour‐enhanced funnel plots [41, 42].

Synthesis methods

Data retrieved from the included studies will be presented in text and tables, in accordance with the recommendations from the Cochrane Prognosis Methods Group, using RevMan [38], and R [42]. We intend to present all included prognostic models listed according to their study of origin, with thorough descriptions of the overall study characteristics and background characteristics of the study participants.

If we identify prognostic models that have undergone robust validation in at least five external validation studies, we will perform meta‐analyses for the model’s discriminatory performance and calibration. A minimum of five studies will be required to ensure appropriate coverage of confidence and prediction intervals in a random‐effects meta‐analysis [43]. Using appropriate transformations (e.g. a logit transformation for C‐statistics) [44], we will report the pooled performance measures with confidence intervals (CIs) and prediction intervals based on a random‐effects approach [36, 41]. We will present meta‐analysis outputs on forest plots. For each meta‐analysis, we will report pooled estimates with 95% CIs and 95% prediction intervals to reflect the expected range of model performance in future settings.

If we need to transform discriminatory statistics prior to meta‐analysis, we will apply the methods reported by Debray and colleagues to estimate C statistics with uncertainty measures [36]. We will subsequently use logit transformations of the C statistics to ensure a normal distribution of data undergoing meta‐analysis [44].

We will not consider model evaluations that use only the development cohort (e.g. random split of data, resampling methods, and internal validation) to be sufficient validation for inclusion in meta‐analyses. However, we will present the results from such efforts in the review text or tables. We also emphasise that we will only perform meta‐analyses when validation is performed in truly external cohorts.

If possible, we will pool information about each model’s discrimination (using C‐statistic or equivalent), calibration (using calibration slope, calibration‐in‐the‐large; and O:E ratio), and equivalents from time‐to‐event models (e.g. Harrell’s C‐statistic, calibration slope, D statistic, O:E at each time point).

For models developed using machine learning techniques, we will use the same synthesis framework applied to other prognostic models. We will prioritise measures of discrimination and calibration for quantitative synthesis, when sufficiently comparable across external validation studies. Threshold‐dependent classification metrics, if reported, will not be pooled with discrimination or calibration measures. We will describe these metrics separately in text or tables only when they provide relevant supplementary information on model performance.

When meta‐analysis is not possible, we will conduct a structured synthesis without meta‐analysis, following the guidance in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions [45]. Studies will be grouped by prediction model, target outcome, study setting, and type of performance measure. We will present the number of studies and participants, model characteristics, validation type, risk of bias, and reported performance measures in structured tables.

Where appropriate, we will summarise the range and distribution of reported performance estimates, such as medians, interquartile ranges, and ranges. We will use visual displays, including forest plots without pooled estimates or other appropriate plots, to support transparent presentation of model performance across studies.

Investigation of heterogeneity and subgroup analysis

Between‐study heterogeneity concerning prognostic models for predicting critically ill patients not yet admitted to the ICU can be attributed to three crucial aspects, as follows.

• Clinical heterogeneity: we will explore differences related to the clinical context and case‐mix, including setting, baseline characteristics of the population, and the timing of predictor assessment. These factors are expected a priori to influence prognostic performance.

• Methodological heterogeneity: we will examine heterogeneity arising from study design and analytical approaches, including whether the model was assessed in development or external validation cohorts, follow‐up periods, and risk‐of‐bias domains. These elements are likely to contribute meaningfully to variation in reported performance.

• Statistical heterogeneity: we will quantify this using Tau².

We will also assess between‐study heterogeneity using the I² statistic, following the guidance in Chapter 10 of the Cochrane Handbook for Systematic Reviews of Interventions [46]. We will consider heterogeneity as follows.

• 0% to 40%: might not be important

• 30% to 60%: may represent moderate heterogeneity

• 50% to 90%: may represent substantial heterogeneity

• 75% to 100%: considerable heterogeneity

We will supplement the statistical heterogeneity assessment with visual inspections of forest plots and assessments of 95% CIs of performance estimations. We will perform these analyses only when the number of studies with reported or derivable performance measures is sufficient (at least 10 studies).

We will perform subgroup analysis only when there are at least five external validation studies within each subgroup being compared. This threshold is intended to maintain consistency with the meta‐analysis criteria and to support more reliable estimation of confidence and prediction intervals.

The following subgroups will be investigated, if possible.

• Geo‐economic classification by income. (For the current 2025 fiscal year, low‐income economies are defined as those with a Gross National Income (GNI) per capita, calculated using the World Bank Atlas method (https://datahelpdesk.worldbank.org), of USD 1145 or less in 2023; lower middle‐income economies are those with a GNI per capita between USD 1146 and USD 4515; upper middle‐income economies are those with a GNI per capita between USD 4516 and USD 14,005; high‐income economies are those with more than a GNI per capita of USD 14,005). We expect this to influence model performance due to differences in healthcare resources.

• Study setting of prognostic model: may affect outcomes and model applicability (participant‐ and outcome‐related heterogeneity) e.g. first assessment in the emergency room versus instability in hospital wards.

• Public services versus private services: monitoring and interventions vary (methodological and contextual heterogeneity)

• Prognostic models applied by nurse‐led versus medical‐led outreach: expertise differences may affect performance (methodological heterogeneity).

Sensitivity analysis

We will perform the following sensitivity analyses.

• Study design: removing studies with retrospective data collections

• Methodological quality: removing studies with results we judge to be at high risk of bias overall

Certainty of the evidence assessment

GRADE guidance for assessing certainty in prognostic model reviews is still evolving. Available GRADE concept papers provide guidance on selected aspects of prognostic model performance, including discrimination and calibration. If further guidance becomes available during the review process, we will follow the most recent guidance. Otherwise, we will adapt the guidance for overall prognosis and prognostic factor studies, together with the available GRADE concept papers for prognostic model performance [47, 48, 49, 50, 51].

For this review, two review authors (AGSV and ACPNP) will independently carry out these assessments. The review authors will resolve any disagreements through discussion or, if necessary, by consulting a third review author (VFMT) for a final decision. The GRADE system classifies the certainty of evidence into one of four grades.

• High certainty will indicate that we are very confident that the reported model performance is close to the true performance in the target population.

• Moderate certainty will indicate that we are moderately confident in the reported model performance, but that the true performance may differ.

• Low certainty will indicate limited confidence in the reported model performance.

• Very low certainty will indicate very limited confidence, with substantial uncertainty about the true performance.

We will consider domains relevant to prognostic models, including phase of investigation (development versus external validation), study limitations (risk of bias), inconsistency of model performance across studies, indirectness, imprecision, and dissemination bias. The certainty of the evidence can be reduced by one (serious concern) or two levels (very serious concern) by the listed domains. Any decision to upgrade certainty will follow emerging GRADE guidance specific to prognostic model performance evidence. Judgements about imprecision will consider the width of CIs around pooled performance measures, the number of external validation studies and events, and whether the uncertainty in estimates would influence conclusions regarding the clinical usefulness or transportability of the mode. This rating will be done for discrimination and calibration performance separately. We will justify all reasons to downgrade or upgrade the certainty rating of studies in footnotes. We will create summary of findings tables for model performance in predicting the following outcomes: admission or transfer to an ICU bed, ICU mortality, hospital mortality, and post‐discharge survival.

We will present the following items in each summary of findings table.

• Model performance across validation studies

• Number of participants

• Number of patients with the outcome

• Certainty of the evidence

Equity considerations

Emergency care and access to intensive care vary significantly between high‐income and LMICs [52, 53, 54]. Bed availability ranges from 0 to 2.8 per 100,000 people in low‐and lower‐middle‐income countries, and rising emergency department visits, mainly due to infectious diseases, overwhelm health systems [55]. In addition, poor infrastructure, including a lack of emergency pharmacies, insufficient water supply, and overcrowding, limit effective triage [56, 57]. This disorderly use of hospital beds wastes financial and human resources and poses serious public health risks.

In this context, ICU admission rates in LMICs are likely to reflect institutional capacity and resource availability in addition to clinical need, representing an important source of heterogeneity that we will explicitly explore in our subgroup analyses [56]. In low‐ and lower‐middle‐income countries, prognostic models are often underutilised because most scoring systems are designed for high‐income settings and require test results that may not be available [22, 58]. Balancing prognostic scores with patients' clinical status is a global challenge. Our review aims to provide reliable information to help decision‐makers effectively reallocate healthcare resources in emergency departments and acute wards. We will conduct subgroup analyses to assess equity in low‐ and middle‐income populations and explore clinical heterogeneity.

Consumer involvement

Patients and other relevant consumers will be involved in the review to ensure that the findings are communicated clearly and are understandable to a non‐specialist audience. Specifically, we will publish the task of reviewing the plain language summary on Cochrane Engage (https://engage.cochrane.org/), and will invite consumers to provide feedback on its clarity, readability, and accessibility. We will incorporate feedback from consumers to refine the plain language summary, thus supporting the production of a transparent and user‐friendly review output.

Supporting Information

Supplementary materials are available with the online version of this article: 10.1002/14651858.CD016115.

Supplementary materials are published alongside the article and contain additional data and information that support or enhance the article. Supplementary materials may not be subject to the same editorial scrutiny as the content of the article and Cochrane has not copyedited, typeset or proofread these materials. The material in these sections has been supplied by the author(s) for publication under a Licence for Publication and the author(s) are solely responsible for the material. Cochrane accordingly gives no representations or warranties of any kind in relation to, and accepts no liability for any reliance on or use of, such material.

Supplementary material 1 Search strategies

New

Additional information

Contributions of authors

Study conceptualisation: Aléxia GS Vieira, Ana CPN Pinto, Amanda AA Garcia, Ricardo K Nawa, Caroline G Mól, Josué DR Duenas, Álvaro N Atallah, Gentle S Shrestha, Marcus J Schultz, Humberto Saconato, and Virginia FM Trevisani.

Search strategy: Aléxia GS Vieira.

Drafting the protocol: Aléxia GS Vieira, Ana CPN Pinto, Amanda AA Garcia, Ricardo K Nawa, Caroline G Mól, Josué DR Duenas, Álvaro N Atallah, Gentle S Shrestha, Marcus J Schultz, Humberto Saconato, and Virginia FM Trevisani.

Critical revision and approval of the protocol: Aléxia GS Vieira, Ana CPN Pinto, Amanda AA Garcia, Ricardo K Nawa, Caroline G Mól, Josué DR Duenas, Álvaro N Atallah, Gentle S Shrestha, Marcus J Schultz, Humberto Saconato, and Virginia FM Trevisani.

Declarations of interest

Aléxia GS Vieira: no commercial or non‐commercial conflicts of interest relevant to this protocol.

Ana CPN Pinto: no commercial or non‐commercial conflicts of interest relevant to this protocol.

Amanda AA Garcia: no commercial or non‐commercial conflicts of interest relevant to this protocol.

Ricardo K Nawa: no commercial or non‐commercial conflicts of interest relevant to this protocol.

Caroline G Mól: no commercial or non‐commercial conflicts of interest relevant to this protocol.

Josué DR Duenas: no commercial or non‐commercial conflicts of interest relevant to this protocol.

Álvaro N Atallah: no commercial or non‐commercial conflicts of interest relevant to this protocol.

Gentle S Shrestha: no commercial or non‐commercial conflicts of interest relevant to this protocol.

Marcus J Schultz: no commercial or non‐commercial conflicts of interest relevant to this protocol.

Humberto Saconato: no commercial or non‐commercial conflicts of interest relevant to this protocol.

Virginia FM Trevisani: no commercial or non‐commercial conflicts of interest relevant to this protocol.

The review authors confirm that they have reviewed Cochrane’s Conflict of Interest policy [59], and will comply with the restrictions described in Section 5.6 for authors of potentially included studies, if applicable.

Sources of support

Internal sources

• Fundação Coordenação de Aperfeiçoamento de Pessoal de Nível Superior (CAPES), Brazil

  In‐kind support for AGSV

External sources

• No internal sources of support received, Other

  Not applicable

Registration and protocol

Cochrane approved the proposal for this first draft in January 2024.

Data, code and other materials

Data sharing is not applicable to this article as it is a protocol, so no datasets were generated or analysed.