Therapeutic hypothermia for newborns with hypoxic‐ischaemic encephalopathy

Objectives

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

To evaluate the benefits and harms of therapeutic hypothermia (TH) compared to standard care in newborn infants with hypoxic‐ischaemic encephalopathy (HIE).

Background

Description of the condition

Perinatal asphyxia results from a lack of oxygen or reduced blood flow during or close to the time of birth. Perinatal asphyxia can lead to multiple organ injuries to the infant, including injury to the heart, liver, or kidneys. The most concerning effects are related to the brain. Perinatal asphyxia may lead to hypoxic‐ischaemic encephalopathy (HIE), which is a leading cause of infant death and disability worldwide. It accounts for over 20% of global neonatal deaths, of which most occur in low‐ and middle‐income countries (LMICs) [1]. The incidence of HIE ranges from 1 to 3 per 1000 live births in high‐income countries, to 1.5 to 20 per 1000 in LMICs [2, 3].

The natural history of HIE includes two phases. The primary phase (primary energy failure) occurs during the initial hypoxic‐ischaemic event and is characterized by a rapid failure of cellular energy production related to a depletion of cellular oxygen stores and a decrease in high‐energy cellular phosphate compounds, such as adenosine triphosphate (ATP) [4, 5]. This leads to immediate cell death, particularly if the insult is severe. The secondary phase (secondary energy failure) begins after blood flow is restored (reperfusion) approximately 7 to 28 hours after the initial insult [6]. The secondary phase involves a complex series of events including reperfusion injury, inflammation, excitotoxicity (over‐excitation of neurons), oxidative stress (an imbalance between the systemic manifestation of reactive oxygen species and a biological system's ability to readily detoxify the reactive intermediates or to repair the resulting damage), and apoptosis (programmed cell death).

The degree of encephalopathy has been evaluated using a variety of clinical tools, including the Sarnat staging [7], Thompson score [8], or other standardized assessment tools [9, 10, 11]. Infants judged to have moderate to severe encephalopathy by these scores have a greater incidence of death or neurodevelopmental impairment [12].

Description of the intervention and how it might work

The goal of therapeutic hypothermia (TH) is to reduce the temperature of the vulnerable deep brain structures in order to reduce the severity of secondary energy failure and therefore prevent further neuronal injury [13]. Several term and preterm animal experimental models have demonstrated that a reduction in brain temperature of 2 °C to 3 °C immediately following a hypoxic‐ischaemic insult reduces energy expenditure, improves subsequent performance testing, reduces histological neuronal loss, or a combination of these [14, 15, 16, 17, 18, 19].

The timing of this intervention is key. Animal studies of newborn sheep cooled to between 30 °C and 33 °C for 72 hours demonstrated protection against death or neurological injury. However, protection was greatest if hypothermia was initiated prior to the onset of seizures [14]. One study suggested that TH in newborn infants with severe HIE was protective against brain injury only if started within six hours of birth [20]. Recent mechanistic work supports this time‑dependent effect [21]. Observational human data similarly indicate reduced magnetic resonance imaging (MRI)‑detected brain injury when cooling is initiated within six hours [22].

Two primary methods of cooling have been utilized in newborn infants with HIE: whole body cooling and selective head cooling with mild systemic hypothermia. In whole body cooling, the infant’s core body temperature is lowered via active means, such as a cooling blanket or fan (manual or servo‐controlled), application of packs containing gel, ice or phase‐changing materials, or via passive means. In selective head cooling, the cooling mechanism is applied directly to the infant’s head, and core body temperature is slightly reduced.

Why it is important to do this review

In infants with moderate to severe HIE, TH has resulted in reduced rates of neuronal injury [23], and in lower rates of mortality and long‐term neurodevelopmental disability [10, 24, 25]. However, its application in clinical practice may differ from that established in the initial randomized controlled trials (RCTs), and it is important to consider safety outcomes (e.g. coagulopathy resulting in major thrombosis or haemorrhage, persistent pulmonary hypertension (PPHN)). Although current findings do not necessarily support its use in these patient groups, in clinical practice hypothermia is also utilized in infants who have a gestational age (GA) below 35 weeks, and in those with mild encephalopathy [26, 27, 28]. Questions about the optimal means to achieve hypothermia are also important, as observational data indicate that infants who are cooled without servo control may experience greater temperature variability and even deep hypothermia [29]. Lastly, the benefits of TH remain unclear in LMICs where resources and comorbidities may differ [30]. Identification of which infants are likely to benefit from TH and in which settings is crucial to guide clinical practice.

This planned Cochrane review will incorporate new methodology compared to the 2013 Cochrane review on TH for newborns with HIE [13]. We will incorporate the data integrity screening tool, developed by Hunter and colleagues [31], to systematically assess the trustworthiness of included trials. This additional step is essential in light of the growing number of publications from unverified or potentially fraudulent sources, which may compromise the validity of evidence synthesis. Implementing a structured integrity assessment will help ensure that only high‐quality, reliable trials contribute to the conclusions of this review. This is particularly important because the findings will inform evidence‐based clinical decision‐making for critically ill newborns, and will help guide policy and practice in neonatal care.

Objectives

To evaluate the benefits and harms of therapeutic hypothermia (TH) compared to standard care in newborn infants with hypoxic‐ischaemic encephalopathy (HIE).

Methods

For the conduct and reporting of this Cochrane protocol, we followed the Cochrane Handbook for Systematic Reviews of Interventions [32], Methodological Expectations of Cochrane Intervention Reviews (MECIR) [33], and PRISMA‐P [34].

Criteria for considering studies for this review

Types of studies

We will include randomized controlled trials (RCTs), quasi‐RCTs, and cluster‐randomized trials. We define quasi‐RCTs as those where the method of allocation is not truly random, but uses an approximation of randomization such as enrolment by patient identification (ID). We will exclude cross‐over trials, since this design is inappropriate for this clinical context.

Types of participants

We will include late preterm (35 weeks + 0 days to 36 weeks + 6 days of gestation) or term newborn infants (≥ 37 weeks + 0 days of gestation) with presumed HIE. For infants or settings where gestational age (GA) is unknown, we will include studies that include infants of at least 2000 g birth weight. We will base presumed HIE on the following.

• Evidence of peripartum asphyxia, as determined by at least one of the following criteria

  • Apgar score of ≤ 5 at 10 minutes

  • mechanical ventilation or resuscitation at 10 minutes

  • cord pH < 7.1, or an arterial pH < 7.1 or base deficit of ≥ 12 within 60 minutes of birth

• Infants with evidence of encephalopathy according to Sarnat staging [7], Thompson score [8], or other standardized assessment tools

The Sarnat score defines severity as follows.

• Stage 1 (mild): hyper‐alertness, hyper‐reflexia, dilated pupils, tachycardia, absence of seizures

• Stage 2 (moderate): lethargy, hyper‐reflexia, miosis, bradycardia, seizures, hypotonia with weak suck and poor Moro reflex

• Stage 3 (severe): stupor, flaccidity, small to mid‐position pupils that react poorly to light, decreased stretch reflexes, hypothermia and absent Moro reflex

The Thompson score is based upon assessment of tone, level of consciousness, presence of seizures, posture, reflexes (Moro, grasp, suck), respirations, and examination of the fontanelle. Mild encephalopathy is defined as a score of 1 to 10, moderate as a score of 11 to 14, and severe as a score of > 15 [8].

Age

We will include hypothermia initiated prior to six hours after birth versus no cooling (standard care). We will also include trials of TH initiated between 6 and 24 hours after birth versus no cooling.

We will exclude infants if they have major congenital abnormalities recognizable at birth.

We will include trials in which only a subset of participants meets the eligibility criteria (e.g. studies including infants < 35 weeks’ gestation alongside late preterm or term infants) only if separate data for the eligible subgroup are available. If subgroup data are not reported, we will include the study only when at least 80% of participants meet the review’s eligibility criteria. We will exclude studies that do not meet either condition [35].

Subgroup analyses will address the method of patient selection, the severity of encephalopathy, and age at initiation of cooling (≤ 6 hours or > 6 hours).

Types of interventions

Intervention

Therapeutic hypothermia by one of the following methods, and offered for more than 24 hours:

• selective head cooling using a servo‐controlled device

• whole body cooling using a servo‐controlled device

• use of ice or phase‐changing material without servo‐control (these could include application to any part of the body including the head)

We will exclude cooling with fans and extracorporeal membrane oxygenation (ECMO) as a modality for cooling. Fan cooling will be excluded because it does not provide reliable or continuous control of core temperature. Infants requiring ECMO represent a distinct clinical population with severe cardiorespiratory failure and multiple concurrent interventions, and are therefore not comparable to infants receiving conventional TH.

Comparison

Therapeutic hypothermia, by any method or approach, compared to standard care (normothermic management). Therapeutic hypothermia typically targets a controlled core temperature of approximately 33 °C to 34 °C, as used in major clinical trials and contemporary clinical guidelines [36]. Normothermic management in neonatal intensive care refers to maintaining a newborn’s body temperature within the normal physiological range of 36.5 °C to 37.5 °C.

Outcome measures

Critical outcomes

• Mortality reported at last follow‐up

• Major neurodevelopmental disability in survivors, defined as the presence of one or more of the following components:

  • cerebral palsy (CP) on clinical examination

  • gross motor impairment (defined as ≥ level 2 according to the Gross Motor Function Classification System (GMFCS) [37]

  • major neurodevelopmental disability assessed in survivors (Bayley or Griffiths assessment, or developmental assessment scales for Indian infants (DASII) [38] or Gesell developmental observation‐revised [39, 40], > two standard deviations (SDs) below the mean; or intellectual impairment or intelligence quotient (IQ) > two SDs below mean [41, 42, 43]); or moderate to severe neurodevelopmental disability or intellectual impairment (IQ > two SDs below mean based upon the Wechsler Preschool and Primary Scale of Intelligence III or IV (WPPSI‐III or IV) for children aged 2 years 6 months to 7 years 7 months [44], or Wechsler International Scale for Children IV or V (WISC IV or V) for those aged 6 to 12 years [44], or Stanford‐Binet Intelligence Scale 5 for children > 2 years old [44])

  • neuromotor delay (Bayley Scales of Infant Development II — Psychomotor Development Index (BSID PDI) or Bayley III Motor Composite, or the Developmental Assessment Scale for Indian Infants – Psychomotor Development Index (DASII PDI))

  • developmental delay (Bayley Scales of Infant Development ‐ Mental Development Index (BSID MDI), the Developmental Assessment Scale for Indian Infants – Mental Development Index (DASII MDI), or a combined assessment of Bayley III Language and Cognitive Composites) [38, 41, 42]

  • neurodevelopment assessed after 18 months (language, cognitive, motor, and overall) standardized continuous scores (e.g. Baileys)

  • blindness (visual acuity < 6/60 in both eyes)

  • sensorineural deafness requiring amplification

• Assessment time points

  • 2 years ± 6 months

  • 2.5 to 5 years

  • > 5 years

We will judge the composite outcome as ‘present’ if we identify any single component outcome, and as ‘not present’ if we do not identify any.

Important outcomes

Short‐term outcomes (up to hospital discharge)

• Mortality at hospital discharge

• Persistent pulmonary hypertension (PPHN)

  • PPHN diagnosed clinically or by echocardiogram

  • requiring inhaled nitric oxide

• Coagulopathy resulting in major thrombosis or haemorrhage or discontinuation of TH

• Blood pressure (hypotension requiring inotrope support)

• Thrombocytopenia (platelet count < 150 x 10⁹/L)

• Renal impairment

  • diagnosis of renal impairment or acute renal failure

  • oliguria (< 1 mL/kg/hour)

• Seizures: seizures during initial hospitalization diagnosed by electroencephalogram (EEG)

• MRI abnormalities (moderate or severe abnormalities in the basal ganglia or thalamus, severe white matter lesions or abnormalities in the posterior limb of the internal capsule, per Rutherford 2010 [45]) assessed in the neonatal period

Longer term developmental outcome

• Predefined subdomains of the composite major neurodevelopmental disability outcome, assessed at:

  • 2 years ± 6 months

  • 2.5 to 5 years

  • > 5 years

These include the following.

• CP on clinical examination

• Gross motor impairment (defined as ≥ level 2 according to the GMFCS [37]

• Major neurodevelopmental disability assessed after 18 months in survivors (Bayley or Griffiths assessment, or DASII [38] or Gesell developmental observation‐revised [39, 40], more than two SD below the mean; or intellectual impairment or IQ more than two SD below mean [41, 42, 43]); or moderate to severe neurodevelopmental disability or intellectual impairment (IQ more than two SDs below mean) based upon WPPSI‐III or IV for children aged 2 years 6 months to 7 years 7 months [44], or WISC IV or V for those aged 6 to 12 years [44], or Stanford‐Binet Intelligence Scale 5 for children over two years old [44]

• Neuromotor delay (BSID PDI or Bayley III Motor Composite, or as DASII PDI)

• Developmental delay (BSID MDI, DASII MDI, or a combined assessment of Bayley III Language and Cognitive Composites) [38, 41, 42]

• Neurodevelopment assessed after 18 months (language, cognitive, motor, and overall) standardized continuous scores (e.g. Baileys)

• Blindness (visual acuity < 6/60 in both eyes)

• Sensorineural deafness requiring amplification

In addition, we will analyse the use of anticonvulsants at follow‐up 2 years ± 6 months.

Search methods for identification of studies

Electronic searches

An Information Specialist (MF) will write the search strategies, which will be conducted without language or publication type limits. We will conduct the searches for trials without date limits, and we will limit searches for systematic reviews to the most recent two years. We will search the following sources.

• Cochrane Central Register of Controlled Trials (CENTRAL), via the Cochrane Register of Studies (CRS)

• Ovid MEDLINE® All, 1946 to Daily Update

• Ovid Embase, 1974 to present

• Ovid Emcare, 1995 to present

• DOAJ (Directory of Open Access Journals) (https://doaj.org/)

A draft MEDLINE strategy, preceded by a search narrative [46], is in Supplementary material 1.

Searching other resources

We will conduct independent searches of the following trial registry.

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

We will not conduct an independent search of ClinicalTrials.gov (clinicaltrials.gov), as three other sources (Embase, CENTRAL, and the WHO ICTRP) include the records. Both Embase and CENTRAL allow for sophisticated searches, unlike the trial registry itself. As such, we are confident we will retrieve the same potentially relevant records.

We will identify conference abstracts in Embase and CENTRAL and by manual searches of the following conferences from the past five years.

• European Academy of Paediatric Societies (EAPS)

• Pediatric Academic Societies (PAS)

• Perinatal Society of Australia and New Zealand (PSANZ)

We will screen the reference lists of included studies and related systematic reviews for studies not identified by the database searches.

We will search for errata or retractions for included studies published on PubMed and the Retraction Watch Database (https://retractiondatabase.org).

Data collection and analysis

If, during the conduct of this review, we identify a study or studies conducted by authors of this Cochrane review, other review authors will independently undertake selection, data extraction, risk of bias, and GRADE assessment of the study or studies. In the event that multiple authors are involved in an included study, we will recruit additional independent colleagues to undertake these tasks, with either authorship or acknowledgement depending on their contributions to the Cochrane review.

Selection of studies

We will manage search results in Endnote [47], and will conduct screening in Covidence [48]. We will use the Covidence RCT Classifier to eliminate known non‐RCTs and to tag possible RCTs [49]. We will report the selection process, including the results of the RCT Classifier, in the ‘Results of the search’ section and the PRISMA diagram [50].

At least two review authors will independently screen titles and abstracts, and will assess the full‐text of references retained following title/abstract screening. We will base decisions for inclusion and exclusion on the Criteria for considering studies for this review. At any point during the screening process, we will resolve disagreements by discussion or by consulting a third review author. We will document the reasons for excluding studies during full‐text review in a ‘Characteristics of excluded studies table’. We will provide any information we can obtain about ongoing studies. Studies with insufficient information upon which to base an inclusion decision will be classified as ‘awaiting assessment’. We will attempt to contact study authors in these instances, but we will list the reference under ‘Studies awaiting assessment’ if we receive no reply.

If we identify studies in languages not read by the review authors, we will first use an online translation service such as Google Translate; we may use two online translation tools to verify the consistency of translations. If we doubt the content of the translation, we will attempt to identify an individual conversant in the language of the report to translate the study.

We will group multiple reports of the same study under a single study ID so that each study, rather than each report, will be the unit of interest in the review.

Data extraction and management

At least two review authors will independently extract and assess the following data.

• Bibliographic details: authors and other citation information; publication status (published/unpublished)

• Methods: trial design; method of randomization

• Administrative details: study design; year(s) in which study was conducted; pre‐registration or protocol details, or both; informed consent information (patient level); ethics approval (institutional); study setting — hospital or care unit type; location (geographic); number of centres; lead author contact information; conflicts/declarations of interest; funding information

• Participant details: number randomized; number lost to follow‐up/withdrawn; number analysed; mean GA; GA range; mean corrected age; corrected age range; inclusion criteria; exclusion criteria

• Interventions: timing of the intervention, such as when it was initiated, frequency, and duration; characteristics of the intervention

• Comparisons

• Outcomes: as outlined in Outcome measures

• Country or countries where the study was conducted and its economic status per World Bank Country and Lending Groups [51].

We will resolve disagreements by discussion or by consulting a third review author. We will develop a data extraction form. We will pilot the data extraction form on a sample of three studies. Where we have questions about data in the study, or where there may be additional, unreported data (such as discreet data for the population of interest in this review), we will contact study authors to request further information. We will note our contact with study authors, and the information below, in the ‘Characteristics of included studies’ section.

We will enter data into RevMan [52]. We will replace any standard error of the mean (SEM) with the corresponding standard error (SE) [53].

Risk of bias assessment in included studies

We will use the Cochrane risk of bias tool, RoB 2, to assess the risk of bias in randomized trials [54, 55]. We will use an RoB 2 Excel tool to implement RoB 2 (www.riskofbias.info/welcome/rob‐2‐0‐tool). The outcomes that we will assess for each study are those described in the Certainty of the evidence assessment section.

At least two review authors will independently assess the risk of bias (low, high, or some concerns) of all included studies. We will resolve any discrepancies in judgment through discussion or by consulting a third review author. We will assess the following types of bias, as outlined in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions [54].

• Bias arising from the randomization process

• Bias due to deviations from intended interventions (we will assess the effect of assignment to the intervention at baseline, i.e. the ‘intention‐to‐treat (ITT) effect’)

• Bias due to missing outcome data

• Bias in measurement of the outcome

• Bias in selection of the reported result

To address these types of bias, we will use the signalling questions recommended in RoB 2 and will make a judgment using the following options.

• ‘Yes’: if there is firm evidence that the question was fulfilled in the study (i.e. the study was at low or high risk of bias given the direction of the question).

• ‘Probably yes’: a judgment was made that the question was fulfilled in the study (i.e. the study was at low or high risk of bias given the direction of the question).

• ‘No’: if there was firm evidence that the question was unfulfilled in the study (i.e. the study was at low or high risk of bias given the direction of the question).

• ‘Probably no’: a judgment was made that the question was unfulfilled in the study (i.e. the study was at low or high risk of bias given the direction of the question).

• ‘No information’: if the study report provided insufficient information to allow any judgment.

We will then use the algorithms proposed by RoB 2 to assign each domain one of the following levels of bias.

• Low risk of bias

• Some concerns

• High risk of bias

This approach will allow the review authors to derive an overall risk of bias rating for each outcome in each study in accordance with the following suggestions.

• ‘Low risk of bias’: we judged the trial at low risk of bias for all domains for this result

• ‘Some concerns’: we judged the trial to raise some concerns in at least one domain for this result, but not as at high risk of bias for any domain

• ‘High risk of bias’: we judged the trial to be at high risk of bias in at least one domain for the result, or we judged the trial to have some concerns for multiple domains such that our confidence in the results is substantially lowered

For cluster‐randomized trials, we will use RoB 2 for cluster‐randomized trials and will follow the guidance in Chapter 23 of the Cochrane Handbook for Systematic Reviews of Interventions [56].

Screening eligible studies for scientific integrity/trustworthiness

We will conduct trustworthiness checks using the ‘Publication‐level/aggregate data checks’ included in the individual participant data (IPD) integrity tool developed by Hunter and colleagues [31], in accordance with the Cochrane policy for managing potentially problematic studies [57]. The tool includes seven aggregate data–level integrity domains: retraction notices and expressions of concern; confirmation of ethics approval from a recognized committee; prospective trial registration or availability of a protocol, or both; randomization and baseline imbalance; plausibility of reported methods and results in relation to the study context and sample size; provision of IPD; and communication with study authors to clarify trial details. Using the tool, at least two review authors will independently assess all studies meeting our inclusion criteria. We will consult a third review author in cases where the decision is unclear, to determine whether a study can be considered sufficiently trustworthy for inclusion in the analysis. In some cases, we may request IPD for a trial to more closely scrutinize potential trustworthiness concerns using the full tool.

We will rate each item below as having either no issues, some/minor issues, or many/major issues. These may be downgraded in severity if specific exemptions apply [31].

Retraction notices and expressions of concern

We will check whether the study of interest or study/studies by the same authors have a retraction notice or Expression of Concern (EOC) in the journal where the study was published, on Retraction Watch (http://retractiondatabase.org/), or on PubPeer (https://pubpeer.com/).

If we identify any major concerns, we will exclude the study from all analyses. In that case, we will not check the additional items below.

Absent or inadequate ethics approval

We will seek an ethics approval letter or details by checking the trial registration record, publication(s), study website, or by direct contact with the trial author(s).

Absent or retrospective trial registration (with or without publicly available protocol)

We will look for the trial registration ID in any study publication(s); will search the WHO ICTRP, ClinicalTrials.gov, and other relevant registers in the WHO Registry Network; and/or directly seek registration details from the trial author(s). We will note registration ID, registration date, dates of first and last participant enrolment, and date of main results publication (if applicable). For retrospectively registered trials, we will note the proportion of participants enroled at the time of registration.

Randomization – balance/imbalance across groups

We will examine the number of participants randomized to each group. We will review the consort diagram or publication text, and will consider whether reasons given for exclusion are plausible.

Plausibility

Implausible recruitment rate

We will check the enrolment period against sample size. We will assess plausibility in the context of facilities available at recruitment centre(s), prevalence of disease/condition in the population, resources/ funding, eligibility criteria, number of collaborators, etc.

Implausible follow‐up

We will check rates of follow‐up across time points, and whether any reasons are given for dropouts. We will consider plausibility in the context of length of follow‐up, target population (disease/ condition, age), setting, sample size, variable, and assessment method.

Implausible results

We will assess the magnitude of results for some key prespecified variables in comparison to similar trials on the same topic and will consider biological mechanisms underlying results. We will consult relevant literature, and will seek advice from clinical or topic experts if needed.

Implausible author group

We will note the number of authors and will consider plausibility relative to study size. We will also check for excessive author productivity (e.g. more than three RCTs published per year as first author) by searching Google Scholar, and check whether the time from study completion to article submission is plausible.

Provision of individual participant data (IPD)

If there are some concerns regarding a study that cannot be resolved from the publication alone, we may request anonymized IPD from the primary investigator/corresponding author, e.g. via email, phone, a mutual connection, or at a conference. If we do not receive any response, we will attempt to contact all other authors. We will look for current email addresses if messages bounce; we will check if IPD are available elsewhere, e.g. journal supplement, data repository. If IPD are provided, we will check whether data for all eligible participants are provided using the trial CONSORT diagram or registration record. We will then apply the IPD level integrity checks from the IPD Integrity Tool [31]. Unavailability of IPD or IPD not supplied upon request will be judged as an integrity concern.

Lack of trial author(s) engagement in communication

Where queries or concerns about a trial arise, we will attempt to contact trial authors for clarification by email, phone, through peers, and in their native language if possible. We may judge failure to clarify any major concerns within a reasonable timeframe as an integrity concern.

Discrepancies between results reported in figures, tables and text (additional standard item from INSPECT‐SR [58])

Where results are reported in multiple places (e.g. figures, tables, text), we will check for discrepancies.

Optional extra items concerning studies where IPD are not available (from INSPECT‐SR [58])

For studies of concern for which we cannot obtain IPD, we may also consider the following aggregate‐level checks.

• Checking whether the means and variances of integer data are impossible using the GRIM [59], or GRIMMER tests [60].

• Checking for errors in statistical results using an online calculator (e.g. https://www.graphpad.com/quickcalcs/ttest1/)

• Checking for plagiarized text using plagiarism software (if available).

Overall assessment

Based on the ratings for each item, we will provide an overall assessment rating for each study as follows.

• No concerns: studies for which there were no concerns or any concerns could be adequately resolved or explained

• Some concerns: studies for which there were some minor concerns that could not be resolved

• Major concerns: studies which have one or more major issues that could not be resolved [31]

We will exclude studies with major concerns from all analyses. Studies with some concerns will be included in sensitivity analyses. However, if their results systematically differ from studies with no concerns, we may exclude them.

Measures of treatment effect

We will perform statistical analysis using RevMan [52], and will undertake meta‐analysis if data is clinically and statistically homogeneous.

For dichotomous data, we will present results using risk ratios (RR) and risk differences (RD), with 95% confidence intervals (CIs). For all outcomes with an estimated RD, we will calculate the number needed to treat for an additional beneficial outcome (NNTB) or the number needed to treat for an additional harmful outcome (NNTH) with 95% CIs, and present these together with the exact P values and the corresponding GRADE certainty of the evidence. We will clearly label NNTB/NNTH values derived from low‐certainty evidence or very‐low certainty evidence.

For continuous data, we will use the mean difference (MD) when outcomes were measured in the same way between trials. We will use the standardized mean difference (SMD) to combine trials that measured the same outcome but used different measurement methods. When trials report continuous data as median and interquartile range (IQR), and data pass the test of skewness, we will convert the median to an approximate mean and estimate the SD as IQR/1.35 [61].

Unit of analysis issues

In individually‐randomized trials, the unit of analysis is the participating infant; an infant will be considered only once in the analysis. In cluster‐randomized trials, the participating neonatal unit or section of a neonatal unit or hospital is the unit of analysis. We will analyse clusters using an estimate of the intracluster correlation coefficient (ICC) derived from the trial (if possible), from a similar trial, or from a study with a similar population, as described in Section 23.1.4 of the Cochrane Handbook for Systematic Reviews of Interventions [56]. If we use ICCs from a similar trial, or from a study with a similar population, we will report this, and conduct a sensitivity analysis to investigate the effect of variation in the ICC.

If we identify both cluster‐randomized trials and individually‐randomized trials, we plan to combine the results from both if there is little heterogeneity between the study designs, and the interaction between the effect of the intervention and the choice of randomization unit is considered to be unlikely.

We will acknowledge any possible heterogeneity in the randomization unit and undertake a sensitivity analysis to investigate possible effects of the randomization unit.

In multi‑arm studies, we will combine intervention arms when more than one arm meets the eligibility criteria so that they form a single pairwise comparison with the control group. If only one intervention arm fulfils the eligibility criteria, we will include that arm and exclude the others. Arm selection will be guided solely by the predefined eligibility criteria.

Dealing with missing data

When feasible, we intend to carry out analysis on an ITT basis for all outcomes. Whenever possible, we will analyse all participants in the treatment group to which they are randomized, regardless of the actual treatment received. If we identify important missing data (in the outcomes) or unclear data, we will request the missing data by contacting the study investigators. We will make explicit assumptions of any methods used to deal with missing data. We plan to perform a sensitivity analysis to assess how sensitive results are to reasonable changes in the undertaken assumptions. We will address the potential impact of missing data on the findings of the review in the ‘Discussion’ section.

Reporting bias assessment

We will assess reporting bias by comparing the stated critical outcomes and important outcomes in the prospective trial registration record or prospectively published protocol against the reported outcomes. Where no such prospective record is available, we will assume a high risk of reporting bias, unless the study was published prior to 2010, in which case we will mark this as unclear. We will document studies using interventions in a potentially eligible infant population, but not reporting on any of the primary and secondary outcomes of interest, in the ‘Characteristics of included studies’ tables.

We plan to use funnel plots to screen for publication bias if more than 10 studies reported the same outcome. If publication bias is suggested by a significant asymmetry of the funnel plot on visual assessment, we plan to incorporate this into our assessment of the certainty of the evidence [62, 63].

Synthesis methods

We will perform meta‐analysis using RevMan [52]. For categorical outcomes, we will calculate the typical estimates of RR and RD, each with its 95% CI; for continuous outcomes, we will calculate the MD or the SMD, each with its 95% CI. We will use a fixed‐effect model to combine data where it is reasonable to assume that studies estimate the same underlying treatment effect. If we judge meta‐analysis to be inappropriate, we will analyse and interpret individual trials separately. If there is evidence of clinical heterogeneity, we will try to explain this based on the different study characteristics and subgroup analyses.

We will examine heterogeneity between trials by inspecting the forest plots and conducting random‐effects analyses as sensitivity analyses, including estimation of Tau². We plan to explore the possible causes of statistical heterogeneity using prespecified subgroup analysis (e.g. differences in study quality, participants, intervention regimens, or outcome assessments).

If we judge meta‐analysis to be inappropriate, we will refer to methodological guidance in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions [64], and Synthesis Without Meta‐analysis (SWiM) reporting guidance [65]. We will create a table with studies ordered by risk of bias, and will calculate standardized effect estimates for each study. This table will be modelled on the worked example as presented in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions [64]. We will use forest plots to provide a graphical representation of the data.

Investigation of heterogeneity and subgroup analysis

Heterogeneity

We will describe the clinical diversity and methodological variability of the evidence in the review text, and with study tables describing study characteristics, including design features, population characteristics, and intervention details.

To assess statistical heterogeneity, we will visually inspect forest plots and describe the direction and magnitude of effects and the degree of overlap between CIs. We will conduct random‐effects analyses as sensitivity analyses, assess Tau² as a measure of heterogeneity, and difference in CIs between fixed‐effect and random‐effects models. We will also consider the statistics generated in forest plots. We will use the I² statistic to quantify inconsistency among the trials in each analysis. If we identify substantial heterogeneity, we will report the finding and explore possible explanatory factors, using prespecified subgroup analysis. Our interpretation will take into account that measures of heterogeneity (Tau²) are estimated with high uncertainty when the number of studies is small [53].

Tests for subgroup differences in effects will be interpreted with caution, given the potential for confounding with other study characteristics and the observational nature of such comparisons [53]. We will consider subgroup analyses with fewer than 10 studies per category as insufficient to reliably detect differences in effects, and we will not highlight any such findings in the results. If subgroup comparisons are possible, we will undertake stratified meta‑analysis and a formal statistical test for interaction to examine subgroup differences that could account for effect heterogeneity (e.g. Cochran’s Q test, meta‐regression) [53, 66].

We will explore high statistical heterogeneity in the outcomes by visually inspecting the forest plots and by removing the outlying studies in the sensitivity analysis [53]. Where statistical heterogeneity is significant, we will interpret the results of the meta‐analyses accordingly and downgrade the certainty of evidence in the summary of findings tables, according to the GRADE recommendations.

We will consider the following groups for subgroup analysis when data is available:

Subgroup analyses

We plan to perform the following subgroup analyses on the effects of the intervention.

• Method of cooling (servo‐controlled whole body cooling, servo‐controlled selective head cooling, manually‐controlled whole body cooling via blanket or ice application)

• Severity of encephalopathy based on Sarnat criteria (mild, moderate, and severe) [7], or Thompson criteria [8]

  • Sarnat:

    • Stage 1 (mild): hyperalertness, hyper‐reflexia, dilated pupils, tachycardia, absence of seizures

    • Stage 2 (moderate): lethargy, hyper‐reflexia, miosis, bradycardia, seizures, hypotonia with weak suck and Moro

    • Stage 3 (severe): stupor, flaccidity, small to mid‐position pupils that react poorly to light, decreased stretch reflexes, hypothermia and absent Moro

  • Thompson:

    • Mild = 1 to 10

    • Moderate = 11 to 14

    • Severe > 15

• GA: the WHO defines preterm birth as any birth before 37 completed weeks of gestation [67]. This is further subdivided on the basis of GA:

  • late preterm infants (restricted to 35 + 0 to 36 + 6 weeks of gestation)

  • term infants (≥ 37 + 0 weeks of gestation)

For studies that report on a broad population of infants (including both preterm infants and term infants), we will categorize the GA of study participants based on the mean GA of participants.

Given that studies in a variety of settings may not have reliable GA and may therefore use birth weight categories, we will include infants categorized as: birth weight ≥ 2500 g, and low birth weight (LBW) infants – defined as infants with birth weight < 2500 g. We will group infants with birth weights between 2000 g to 2500 g with late preterm infants, and those with birth weight ≥ 2500 g with the term infants.

For studies that report on a broad population of infants (including both preterm infants and term infants), we will attempt to only extract data for our eligible population, if data are reported in strata. If only combined data are reported, we will include studies that have a preponderance of late‐term and term infants (> 80% of infants).

• Based on GA and birth weight, we will consider subgroup analyses for infants defined as:

  • small for GA, normal weight, large for GA;

• Age at initiation of cooling (≤ 6 hours or > 6 hours);

• Setting: low‐ and middle‐income settings, based on World Bank country classifications (newborns born in under‐resourced countries (low‐and middle‐income) versus in other country settings (high‐income) versus mixed or not reported) [51];

• Infant sex (male, female, other)

We will interpret these results with caution given the potential for confounding with other study characteristics and the observational nature of the comparisons.

Equity‐related assessment

We consulted the PROGRESS‐Plus framework, which outlines population characteristics that may factor into health equity/inequity [68]. We plan to document two factors: study location (which maps to ‘place of residence’ in the PROGRESS‐Plus framework) and sex. We will categorize study locations according to the World Bank Country and Lending Group classification scheme [51] (e.g. low‐, lower‐middle‐, upper‐middle‐, and high‐income economies), and document this in the ‘Characteristics of included studies’ tables. We will conduct subgroup analysis by economic classification, and sex to determine if outcomes differ for either factor. In addition, we will qualitatively report on characteristics of participants included and excluded in the identified RCTs, to assess which populations our findings may or may not be generalizable to.

Sensitivity analysis

We will report results of sensitivity analyses for critical outcomes only. Since there is no formal statistical test that can be used for sensitivity analysis, we will provide informal comparisons between the different ways of estimating the effect under different assumptions. Changes in the P values will not be used to judge whether there is a difference between the main analysis and sensitivity analysis, since statistical significance may be lost when fewer studies are included. We will report the results of the sensitivity analyses in tables, rather than in forest plots [53].

To compare fixed‑effect and random‑effects models, we will implement random‑effects meta‑analysis using the Restricted Maximum Likelihood (REML) estimator to estimate between‑study variance. For the calculation of CIs, we will use the Hartung‑Knapp‑Sidik‑Jonkman method when at least three studies are included and the estimated heterogeneity is greater than zero. In analyses including only two studies, or when the estimated heterogeneity is zero, we will use the standard Wald‑type CI [69].

In TH trials, blinding of participants and personnel is not feasible. Consequently, we expect to rate all studies at high risk of bias in the RoB 2 domain ‘bias due to deviations from intended interventions’. As this domain does not differentiate between studies, it is not informative for sensitivity analyses. We will therefore conduct a sensitivity analysis excluding studies judged to be at high risk of bias in any of the other RoB 2 domains. We will only include studies that we assess as having low risk of bias in all remaining domains in this sensitivity analysis, to evaluate the robustness of the findings.

For cluster‐RCTs, we plan to conduct a sensitivity analysis to investigate the effect of variation in the ICC, as reported in the Unit of analysis issues section. We plan to undertake a sensitivity analysis to investigate possible effects of the randomization unit, as reported in the Unit of analysis issues section. For missing data, we plan to perform a sensitivity analysis to assess how sensitive results are to reasonable changes in the undertaken assumptions (Dealing with missing data). In the case of high statistical heterogeneity in the outcomes, we plan to remove the outlying studies from the sensitivity analysis, as reported in the Investigation of heterogeneity and subgroup analysis section.

Certainty of the evidence assessment

We will use the GRADE approach to assess the certainty of evidence, as outlined in the Handbook for Grading the Quality of Evidence and the Strength of Recommendations [70], and the Cochrane Handbook for Systematic Reviews of Interventions [71, 72], for the following critical outcomes (as defined in Critical outcomes section).

• Mortality reported at last follow‐up

• Major neurodevelopmental disability at 2 years (± 6 months) in survivors

We will also assess the certainty of the evidence for the following important outcomes (as defined in Important outcomes section).

• Longer term developmental outcome at 2 years (± 6 months)

  • CP on clinical examination

  • gross motor impairment

  • major neurodevelopmental disability

• Short‐term outcomes (up to hospital discharge)

  • PPHN

    • PPHN diagnosed clinically or by echocardiogram

    • requiring inhaled nitric oxide

  • coagulopathy resulting in major thrombosis or haemorrhage or discontinuation of TH

Two review authors will independently assess the certainty of the evidence for each outcome. We will resolve disagreements by consensus or by consulting a third review author. We will consider evidence from RCTs as high certainty, and will downgrade the certainty of the evidence by one level for serious (or two levels for very serious) limitations based upon the following: design (risk of bias), consistency across studies, directness of the evidence, precision of estimates, and presence of publication bias. We will use GRADEpro GDT software to create and display a summary of findings table [73], to report the certainty of the evidence for the following comparison: any form of TH versus standard care (normothermic management).

The GRADE approach results in an assessment of the certainty of a body of evidence as one of the following four grades.

• High: we are very confident that the true effect lies close to that of the estimate of the effect.

• Moderate: we are moderately confident in the effect estimate; the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.

• Low: our confidence in the effect estimate is limited; the true effect may be substantially different from the estimate of the effect.

• Very low: we have very little confidence in the effect estimate; the true effect is likely to be substantially different from the estimate of effect.

We will justify all decisions to downgrade the certainty of the evidence using footnotes and make comments to aid the reader's understanding of the review where necessary.

Consumer involvement

We selected the critical and important outcomes based on a core outcome set developed using the Context, Observation, Impact, Next steps (COIN) process [74]. A steering group that involved parents of infants requiring neonatal care developed these outcomes [75]. We will engage families from Hope for HIE [76], which is a parent‐founded and parent‐led organization whose mission is to improve the quality of life for children and families affected by neonatal and paediatric‐acquired HIE through awareness, advocacy, education, research, and support. Individuals from Hope for HIE will join the review authorship team to contribute to the interpretation of the findings and to aid dissemination of the results.

Supporting Information

Supplementary materials are available with the online version of this article: 10.1002/14651858.CD016345.

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

These authors should be considered joint first author

New

Additional information

Contributions of authors

AF, ALS, and RFS conceived, coordinated, and led the protocol.

AF, MTB, RFS, KH, JA, JS, MB, and ALS undertook the research to inform the objectives, background, and inclusion criteria.

MF designed the literature search methods and performed the literature searches.

All protocol authors were involved in designing the other methods sections, and writing and editing the protocol text. All authors read and approved the final protocol version prior to publication.

This is a new Cochrane protocol. However, the topic evolved from a 2013 Cochrane review [13]. Three authors of this Cochrane protocol were coauthors of the 2013 Cochrane review, namely MTB, RFS, and JS. The content of this Cochrane protocol may include some information from the 2013 Cochrane review.

Declarations of interest

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

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

RFS: is the Co‐ordinating Editor of Cochrane Neonatal, Vice President and Director of Clinical Trials of the Vermont Oxford Network, and Professor at the Larner College of Medicine, University of Vermont. He took no part in the editorial processes for this protocol. He has no commercial or non‐commercial conflicts relevant to this protocol.

MF: is a Managing Editor and Information Specialist with the Cochrane Neonatal Review Group; she took no part in the editorial assessment or acceptance of this protocol. She has no commercial or non‐commercial conflicts relevant to this protocol.

KH: is Associate Convenor of the Cochrane Prospective Meta‐Analysis Methods Group and a member of the Cochrane Methods Executive. She has no commercial or non‐commercial conflicts relevant to this protocol.

JA: no commercial or non‐commercial conflicts of interest relevant to this protocol

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

JC: is a Managing Editor with the Cochrane Neonatal Review Group; she took no part in the editorial assessment or acceptance of this protocol. She has no commercial or non‐commercial conflicts relevant to this protocol.

MB: is an Associate Editor for the Cochrane Neonatal Group. However, he took no part in the editorial processing of this review. He has no commercial or non‐commercial conflicts relevant to this protocol.

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

Sources of support

Internal sources

• Institute for Clinical Sciences, Lund University; Research & Development, Skåne University Hospital, Lund, Sweden

  MB is employed by this organization.

• University Medical Center Rostock, Germany

  AF, JA, and ALS are employed by this institute.

External sources

• Region Skåne, Skåne University Hospital and Lund University, Sweden

  Cochrane Sweden received support from Region Skåne, Skåne University Hospital and Lund University

• Vermont Oxford Network, USA

  Cochrane Neonatal Reviews are produced with support from Vermont Oxford Network, a worldwide collaboration of health professionals dedicated to providing evidence‐based care of the highest quality for newborn infants and their families.

Registration and protocol

Cochrane approved the proposal for this protocol in July 2025.

Data, code and other materials

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