Early versus late surgical start times for on‐pump cardiac surgery 

Objectives

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

To assess the effects of early versus late surgical start times for on‐pump cardiac surgery on mortality, cardiac outcomes, and quality of life.

Background

Description of the condition

Approximately 275,000 to 300,000 cardiac surgical procedures have been performed annually in the USA over the past decade, the bulk of which being coronary artery bypass grafting, aortic or mitral valve procedures, or combinations of the above (Bowdish 2020). In the USA, the cost of cardiac surgery is approximately 0.6% of the USD 3.6 trillion annual total healthcare expenditure, USD 6.5 billion of which are costs attributable to coronary artery bypass grafting alone (Centers for Medicare & Medicaid Services 2019; Guduguntla 2018; Senst 2020). Globally, an estimated 10,000 cardiothoracic surgeons perform more than 2 million cardiac surgical procedures per year across 6000 medical centres (Zilla 2018).

Traditionally, cardiac surgical procedures have occurred under cardiopulmonary bypass; however, off‐pump and minimally invasive techniques are alternatives in certain procedures depending on patient characteristics. One of the limitations of the cardiopulmonary bypass approach is the inevitability of some degree of residual perioperative ischaemia‐reperfusion injury, as indicated by a post‐operative troponin rise. Clinically, ischaemia‐reperfusion injury can contribute to postoperative adverse cardiac events such as atrial fibrillation, myocardial stunning and dysfunction, myocardial infarction, and cardiac death (Liu 2020; Turer 2010).

Description of the intervention

Circadian variations in human physiology are well established and influence manifold systems including the autonomic nervous system (Burgess 1997), endocrine function (Gamble 2014), neurocognition (Schmidt 2007), and placental function (Waddell 2012). Circadian rhythms also influence pathophysiological states including the efficacy of bronchodilators in airways disease (Calverley 2003), and arousal in Parkinson’s disease (Videnovic 2014). Importantly, an association between time of day and the incidence and severity of cardiovascular disease has also been established. Acute myocardial infarction, sudden cardiac death, and ischaemic stroke all display a morning predilection(Alibhai 2015; Muller 1991; Willich 1992), while an effect between daytime variation and infarct size post‐ST‐elevation myocardial infarction has been variably reported (Ammirati 2013; Bulluck 2017; Fournier 2012; Reiter 2012; Suarez‐Barrientos 2011). Given these associations between circadian rhythm and cardiovascular outcomes, there has been increasing interest in circadian influences on outcomes after cardiac surgery.

How the intervention might work

In late 2017, Montaigne and colleaguespublished the first report of significantly improved outcomes in patients undergoing cardiac surgery in the afternoon compared to the morning (Montaigne 2018). The evidence for this finding included both a prospective observational study (of 596 patients undergoing aortic valve replacement) as well as a randomised trial (of 44 patients randomised to morning isolated aortic valve replacement and 44 randomised to afternoon surgery). The observational study demonstrated that at a median of 500 days' follow‐up, the frequency of major adverse cardiac events (defined as cardiovascular death, myocardial infarction, and admission to hospital for acute heart failure) were lower in the afternoon group compared to the morning group, translating to one major adverse cardiac event prevented for every 11 patients operated on in the afternoon compared to in the morning. This finding was driven mainly by reductions in rates of both perioperative myocardial infarction and acute heart failure. The randomised controlled trial (RCT) showed that until hospital discharge (median follow‐up 12 days), the geometric mean of perioperative cardiac troponin T release was significantly lower in the afternoon group compared with the morning group. These results were published concurrently with experimental studies on human atrial tissue and mouse heart models, which provide mechanistic understandings. The putative mechanism for a protective effect with afternoon surgery centred around a differential, time‐of‐day‐dependent tolerance to ischaemia‐reperfusion injury that was worse in the atrial samples of patients who underwent morning surgery. Transcriptomic analysis (analysis of transcriptional activity, including both coding and non‐coding RNAs) revealed a significantly higher expression of the nuclear receptor and transcriptional repressor Rev‐Erbα – a circadian clock protein – in the morning samples. Experimental inhibition of Rev‐Erbα in mouse hearts was shown to minimise ischaemia‐reperfusion injury via increasing the downstream effector protein CDKN1a/p21, an inhibitor of hypoxia‐induced apoptosis (Adachi 2001). Accordingly, down‐regulation of the clock protein Rev‐Erbα in the afternoon may lead to protection from hypoxia‐induced apoptosis in cardiac myocytes and potentially improved surgical outcomes.

Why it is important to do this review

Since 2017, other studies have sought to replicate Montaigne and colleague’s findings with mixed results. Given the practice‐altering potential of conclusive findings, consensus is needed regarding whether or not time‐of‐day variations exert significant influences on important clinical outcomes following cardiac surgery. 

Objectives

To assess the effects of early versus late surgical start times for on‐pump cardiac surgery on mortality, cardiac outcomes, and quality of life.

Methods

Criteria for considering studies for this review

Types of studies

We will include RCTs and cluster‐RCTs. We will not include quasi‐randomised studies as they are not true randomised studies. Cross‐over trials are inappropriate by nature of the intervention.

We will include studies reported as full text, those published as abstract only, and unpublished data.

Types of participants

We will include adults (18 years of age and older) undergoing on‐pump cardiac surgery. Cardiac surgery will be defined as any surgery performed on the heart and great vessels, including the thoracic aorta.

We will exclude paediatric populations. Paediatric cardiac surgery is considerably heterogeneous compared to adult cardiac surgery. Significant anatomical and physiological differences mean that any underlying pathophysiological mechanisms may not be meaningfully comparable.

Where studies include only a subset of relevant participants, we will only incorporate that eligible subset of participants into our review. Where eligible participants are inseparable from ineligible participants, we will contact study authors to obtain unpublished data for eligible participants only. Where we cannot obtain such data, we will document the circumstances descriptively as part of the narrative.

Types of interventions

We will aim to include any study that investigates the effect of different surgical start times on outcomes. We anticipate that these studies may fall into the following groups:

• early versus late, defined by a 12 pm surgical start time cut‐off; and

• surgical start time as a categorical rather than dichotomised variable.

Where studies with dichotomous reporting do not report a cut‐off time for differentiating early versus late surgical start time, we will include the study in the review and carry out a sensitivity analysis to investigate the effect of removing these studies on pooled estimates.

We will analyse studies with dichotomous reporting that use a cut‐off time other than 12 pm separately and provide a narrative summary of findings.

We will not include studies that solely investigate the effect of weekend versus weekday start times.

Types of outcome measures

It is not necessary for studies to report one or more of the outcomes listed here to be eligible for inclusion in the review. Where a published report does not appear to report one of these outcomes, we will access the trial protocol and contact the trial authors to ascertain whether the outcomes were measured but not reported. Relevant studies, which measured these outcomes but did not report the data at all, or not in a usable format, will be included in the review as part of the narrative.

Primary outcomes

1. Short‐term mortality (≤ 30 days postoperative)

2. Long‐term mortality (> 30 days postoperative)

3. Perioperative myocardial infarction (Thygesen 2018)

Secondary outcomes

Standard Society of Thoracic Surgeons’ definitions for postoperative events and complications where applicable (Society of Thoracic Surgeons 2020).

1. Perioperative myocardial injury (as measured by troponin change, ng/mL; Thygesen 2018)

2. New‐onset postoperative atrial fibrillation during hospital stay

3. Left ventricular ejection fraction at discharge (%)

4. Length of intensive care unit (ICU) admission (hours)

5. Length of hospital stay (days)

6. Quality of life, measured prior to cardiac surgery and followed up within 30 days postoperative, 1 year postoperative, and long term (more than 1 year postoperative). Eligible quality‐of‐life scales will include:

   1. generic scales such as the:

      1. short form health survey (SF‐36 (Ware 1992) or SF‐12 (Jenkinson 1997)) and

      2. Nottingham Health Profile (NHP) (Hunt 1981), as well as

   2. disease‐specific scales such as the:

      1. Duke Activity Status Index (DASI) (Hlatky 1989) and

      2. HeartQOL (Oldridge 2014).

Search methods for identification of studies

Electronic searches

We will identify studies through systematic searches of the following bibliographic databases:

1. Cochrane Central Register of Controlled Trials (CENTRAL; current year and issue) in the Cochrane Library

2. MEDLINE (Ovid, from 1946 onwards)

3. Embase (Ovid, from 1980 onwards)

4. Web of Science CPCI‐S (Conference Proceedings Citation Index ‐ Science) (from 1990 onwards)

The preliminary search strategy for MEDLINE (Ovid) (Appendix 1) will be adapted for use in the other databases. The Cochrane sensitivity‐maximising RCT filter (Lefebvre 2021), will be applied to MEDLINE (Ovid) and adaptations of it to the other databases, except CENTRAL.

We will also conduct a search of ClinicalTrials.gov (www.ClinicalTrials.gov) and the WHO International Clinical Trials Registry Platform (ICTRP) Search Portal (apps.who.int/trialsearch/) for ongoing or unpublished studies.

We will search all databases from their inception to the present, and we will impose no restriction on language of publication or publication status.

We will not perform a separate search for adverse effects of early versus late surgical start time. We will consider adverse effects described in included studies only.

Searching other resources

We will check reference lists of all included studies and any relevant systematic reviews identified for additional references to studies. We will examine any relevant retraction statements and errata for included studies. We will contact authors of potentially relevant studies for missing data where these data are deemed potentially relevant to our review objective. We will also perform a Google Scholar search with key words to identify further potentially pertinent studies.

Data collection and analysis

Selection of studies

Two review authors (MN and MP) will independently screen titles and abstracts for inclusion of all the potential studies we identify as a result of the search and code them as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. If there are any disagreements, a third author will be asked to arbitrate (JAS). We will retrieve the full‐text study reports/publication and two review authors (MN and MP) will independently screen the full text and identify studies for inclusion, and identify and record reasons for exclusion of the ineligible studies. We will resolve any disagreement through discussion or, if required, we will consult a third review author (JAS). We will identify and exclude duplicates and 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 record the selection process in sufficient detail to complete a PRISMA flow diagram (Page 2021), and 'Characteristics of excluded studies' table.

Data extraction and management

We will use a data collection form for study characteristics and outcome data which has been piloted on at least one study in the review. Two review authors (MN and MP) will independently extract study characteristics from included studies. Where applicable, we will extract the following study characteristics.

1. Methods: study design, total duration of study, number of study centres and location, study setting, and date of study

2. Participants: number randomised, number lost to follow‐up/withdrawn, number analysed, mean age, age range, gender, severity of condition, diagnostic criteria, inclusion criteria, exclusion criteria, and follow‐up time. We will also record population baseline characteristics, operation details, and preoperative history of co‐morbidities

3. Interventions: intervention, comparison, concomitant medications, excluded medications, and cut‐off time for early versus late group dichotomisation

4. Outcomes: primary and secondary outcomes specified and collected, and time points reported

5. Notes: funding for study, and notable conflicts of interest of study authors

Two review authors (MN and MP) will independently extract outcome data from included studies. We will resolve disagreements by consensus or by involving a third person (JAS). One review author (MN) will transfer data into Review Manager Web (RevMan Web 2022). We will double‐check that data are entered correctly by comparing the data presented in the systematic review with the data extraction form. A second review author (MP) will spot‐check study characteristics for accuracy against the study report.

Assessment of risk of bias in included studies

Two review authors (MN and MP) will independently assess risk of bias for each study using RoB2, outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021a). We will resolve any disagreements by discussion or by involving another author (JAS). We will assess the risk of bias of a specific result of a study according to the following domains:

1. bias arising from the randomisation process;

2. bias due to deviations from intended interventions;

3. bias due to missing outcome data;

4. bias in measurement of the outcome; and

5. bias in selection of the reported result.

For cluster‐RCTs, we will assess the risk of bias of a specific result of a study according to the following domains, in keeping with the latest methodological guidance (Eldridge 2021):

1. bias arising from the randomisation process;

2. bias arising from the identification or recruitment of participants into clusters;

3. bias due to deviations from intended intervention;

4. bias due to missing outcome data;

5. bias in measurement of the outcome; and

6. bias in selection of the reported result.

We will assess the risk of bias for the outcomes of the included studies in our summary of findings table.

We are interested in quantifying the effect of assignment to the interventions at baseline, regardless of whether the interventions are received as intended (the ‘intention‐to‐treat effect’).

We will use the signalling questions in RoB 2 and rate each domain as 'low risk of bias', 'some concerns' or 'high risk of bias'. We will summarise the risk of bias judgements across different studies for each of the domains listed for each outcome. The overall risk of bias for the result is the least favourable assessment across the domains of bias.

We plan to use the RoB2 Excel tool (sites.google.com/site/riskofbiastool/welcome/rob-2-0-tool/current-version-of-rob-2) to manage the assessment of bias.

The detailed RoB 2 data will be stored as supplementary data.

When considering treatment effects, we will take into account the risk of bias for the studies that contribute to that outcome.

Measures of treatment effect

We will analyse dichotomous data as risk ratios with 95% confidence intervals, and continuous data as mean difference or standardised mean difference with 95% confidence intervals.

Where studies report the same outcome and unit of measure we will use mean differences. We will use standardised mean differences where studies do not use the exact same outcome measure. We will enter data presented as a scale with a consistent direction of effect.

We will interpret standardised mean differences based on benchmarks suggested by Cohen (Cohen 1988), with effect sizes as small (standardised mean difference = 0.2), medium (standardised mean difference = 0.5), and large (standardised mean difference = 0.8).

When analysing continuous outcomes as mean differences, we define the following as minimal clinically important differences.

1. Perioperative myocardial injury (as measured by troponin change, ng/mL) 3.8 ng/L (Täger 2019)

2. Left ventricular ejection fraction at discharge (%) 5% (Solomon 2005)

3. Length of ICU admission (hours) 12 hours

4. Length of hospital stay (days) 1 day

In the absence of guidance literature in the perioperative setting, we adopted the minimal clinically important difference for troponin change proposed by Täger 2019, noting that this study was performed in the outpatient setting and may not fully translate to the perioperative setting. The minimal clinically important differences for lengths of ICU admission and hospital stay were decided by author consensus, in the absence of applicable guidance literature.

We will narratively describe skewed data reported as medians and interquartile ranges.

Unit of analysis issues

Where we include RCTs with parallel design, we will define different outcomes based on different periods of follow‐up and plan separate analyses to address issues around repeated observations on participants.

Where studies compare more than two interventional groups (e.g. morning versus afternoon versus evening surgical start times), we will follow advice in the Cochrane Handbook for Systematic Reviews of Interventions to analyse multiple intervention groups in an appropriate way that avoids arbitrary omission of relevant groups and double‐counting of participants (Higgins 2021b).

Where cluster‐RCTs are included, we will use methods described in the Cochrane Handbook for Systematic Reviews of Interventions to account for clustering in the data to avoid an inappropriately high level of precision in the analysis (Higgins 2021c).

Cross‐over trial designs are inappropriate by nature of the intervention.

Dealing with missing data

We will contact investigators or study sponsors in order to verify key study characteristics and obtain missing numerical outcome data where possible (e.g. when a study is identified as abstract only). Where possible, we will use the Review Manager Web calculator (RevMan Web 2022), to calculate missing standard deviations using other data from the study, such as confidence intervals, based on methods outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021b). Where this is not possible, and the missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results by a sensitivity analysis.

Assessment of heterogeneity

We will inspect forest plots visually to consider the direction and magnitude of effects and the degree of overlap between confidence intervals. We will use the I² statistic (Higgins 2003), to measure heterogeneity among the studies in each analysis, but acknowledge that there is substantial uncertainty in the value of the I² statistic when there is only a small number of studies. We will also consider the P value from the Chi² test.

Substantial heterogeneity will be defined as per the Cochrane Handbook for Systematic Reviews of Interventions, where I² statistic values are 50% or greater (Deeks 2021). However, we will interpret importance of the observed I² statistic value in light of the strength of evidence for heterogeneity (e.g. P value from the Chi² test, or a confidence interval for I² statistic). Uncertainty in the value of the I² statistic is substantial when the number of studies is small (Deeks 2021). 

If we identify substantial heterogeneity, we will report it and explore possible causes by prespecified subgroup analysis.

Assessment of reporting biases

If we are able to pool more than 10 studies, we will create and examine a funnel plot to explore possible small study biases for the primary outcomes. We will also perform a formal statistical test for asymmetry (e.g. Egger 1997). If we have a small number of studies however, we acknowledge that the ability to detect publication bias is largely diminished, so it is difficult to exclude the presence of publication bias.

Data synthesis

We will undertake meta‐analyses only where this is meaningful, that is, if the treatments, participants and the underlying clinical question are similar enough for pooling to make sense (Deeks 2021).

Study estimations of circadian effects (if present) may follow a distribution across studies. This may be influenced by population characteristics, study location (and distance from the equator), number of included centres, and other variations in surgical technique and study methodology. Hence, we will use a random‐effects model.

The primary analysis will include all eligible studies.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses for any outcomes with substantial heterogeneity, where there is a minimum of 10 studies included in the analysis.

1. Studies grouped on type of surgery (e.g. coronary artery bypass grafting, valve surgery subtypes, thoracic aorta surgery, combinations of the above, other cardiac surgeries)

2. Studies grouped study design (e.g. single centre vs multicentre)

3. Studies grouped by case urgency (elective, urgent, emergent)

We will use the formal test for subgroup differences in Review Manager Web (RevMan Web 2022).

Sensitivity analysis

We plan to carry out the following sensitivity analyses, to test whether key methodological factors or decisions have affected the main result.

1. Sensitivity analyses including only studies that are overall low risk of bias/some concerns, removing studies identified as high risk of bias

2. Sensitivity analyses removing all participants undergoing thoracic aorta surgery without heart surgery, assessing whether or not protective circadian mechanisms are limited to surgery on the heart itself

3. Sensitivity analyses removing all studies with incompletely reported outcome data

Summary of findings and assessment of the certainty of the evidence

We will create a summary of findings table using the following outcomes: short‐term mortality, long‐term mortality, perioperative myocardial infarction during hospital stay, length of hospital stay, and quality of life at 1 year. We will use the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the certainty of a body of evidence. We will use the overall RoB2 judgements for GRADE assessments. We will use methods and recommendations described in Chapter 14 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2021), using GRADEpro GDT software.

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

Two review author (MN and MP), working independently, will make judgements about evidence quality, with disagreements resolved by discussion or by involving a third review author (JAS). We will justify and document judgements, and incorporate them into reporting of results for each outcome.

Appendices

Appendix 1. Preliminary MEDLINE (Ovid) search strategy

1     exp Cardiac Surgical Procedures/

2     ((cardiac or cardio* or heart or coronary or valv*) adj2 (surgery or surgeries or surgical or procedure* or operat* or bypass)).tw. 

3     Cardiopulmonary Bypass/ 

4     cardiopulmonary bypass.tw.

5     cpb.tw.

6     (CABS or CABG or CAGS).tw.

7     or/1‐6

8     exp Biological Clocks/ or Circadian Rhythm/

9     ((circadian or diurnal or daytime or (tim* adj3 day) or (tim* adj3 surg*)) adj4 (variation* or fluctuat* or disturb* or rhythm* or oscillation* or influenc* or impact* or effect* or affect* or depend* or differen* or assoc*)).tw.

10     (start* adj3 tim*).tw.

11     ((afternoon* or PM or night*) adj4 (morning* or AM or day*)).tw.

12     or/8‐11

13     7 and 12

14     randomized controlled trial.pt.

15     controlled clinical trial.pt.

16     randomized.ab.

17     placebo.ab.

18     drug therapy.fs.

19     randomly.ab. 

20     trial.ab. 

21     groups.ab.

22     14 or 15 or 16 or 17 or 18 or 19 or 20 or 21

23     exp animals/ not humans.sh.

24     22 not 23 

25     13 and 24

Contributions of authors

ZL, LAP and JCP‐D designed the project. ZL drafted the manuscript. All review authors contributed to critical revisions of the manuscript.

Sources of support

Internal sources

• No sources of support provided

External sources

• NIHR, UK

  This project was supported by the NIHR via Cochrane Infrastructure funding to the Heart Group. The views and opinions expressed therein are those of the authors and do not necessarily reflect those of the Systematic Reviews Programme, NIHR, NHS or the Department of Health and Social Care.

Declarations of interest

Z Liu: our authorship group is currently planning 2 observational studies that will not be eligible for inclusion in this review once published. Based on the results of these 2 observational studies and this review once published, we will then conduct a randomised controlled trial on this topic. We declare no funding for any of these works.

JC Penny‐Dimri: our authorship group is currently planning 2 observational studies that will not be eligible for inclusion in this review once published. Based on the results of these 2 observational studies and this review once published, we will then conduct a randomised controlled trial on this topic. We declare no funding for any of these works.

M Nagel: no conflict

M Plummer: no conflict

R Segal: unrestricted educational grants from F&P, Abbvie, MSD, Ambu, Storz to institution. Honoraria for presentations from Abbvie and F&P to institution. These companies have no interest in this topic. Support for attending meeting by Storz and F&P to institution.  Income from private practice.

P Morley: no conflicts

J Smith: no conflicts

L Perry: our authorship group is currently planning 2 observational studies that will not be eligible for inclusion in this review once published. Based on the results of these 2 observational studies and this review once published, we will then conduct a randomised controlled trial on this topic. We declare no funding for any of these works.

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