Stem cell therapy for dilated cardiomyopathy

Abstract

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

To assess the efficacy and safety of stem cell therapy (SCT) in adults with non‐ischaemic dilated cardiomyopathy (DCM).

Background

Description of the condition

Dilated cardiomyopathy (DCM), also known as non‐ischaemic DCM, is a heart muscle disorder defined by the presence of left ventricular or biventricular systolic dysfunction and dilatation in the absence of hypertension, valvular, congenital, or ischaemic heart disease (Bozkurt 2016; Pinto 2016). DCM is the most common form of non‐ischaemic cardiomyopathy worldwide (Jefferies 2010: McKenna 2017), and represents one of the leading causes of the need for heart transplantation in adults (Merlo 2016; Stehlik 2011). DCM was first described by the World Health Organization (WHO) in 1980 (WHO/ISFC 1980), and its prevalence is estimated at 1 in 2500 (Hershberger 2013). Most patients with DCM present with symptoms of heart failure, including dyspnoea and fatigue on exertion, orthopnoea, ankle oedema and excessive sweating (Dec 1994; Weintraub 2017). Survival in patients with DCM is extremely poor after the diagnosis, and early studies have shown that most deaths occur within the first two years of follow‐up (Díaz 1987; Fuster 1981). Optimal medical therapy as a first‐line treatment, either with or without device therapy (Ponikowski 2016; Yancy 2013), has progressively and significantly improved the long‐term prognosis of DCM over the past three decades (Merlo 2014). However, although a proportion of patients recover cardiac function, in the long term there is a trend towards worsening of left ventricular function (Merlo 2015). Cardiac transplantation is reserved for extremely ill patients and for those needing continuous intravenous inotrope support, mechanical ventilatory support or ventricular assist device support (Jefferies 2010). The use of stem cell therapy (SCT) may be an alternative treatment to reduce or stop further deterioration of left ventricular function in patients with end‐stage DCM. However, two recent systematic reviews have shown some benefits in terms of systolic function and mortality but not in exercise tolerance (Lu 2016; Marquis‐Gravel 2014).

Description of the intervention

Stem cells are types of cells with special characteristics, such as proliferation, self‐renewal, regeneration and the possibility of generating different lineages of differentiated progeny (Blau 2001). These features have prompted the development of SCT. The objective of SCT in the treatment of DCM is to achieve cardiac muscle regeneration and recovery of functional capacity, either by replacing the dead myocardium or by activating physiological repair mechanisms (Menasché 2018). The first description of cell transplantation into the human myocardium was a case report published in 2001 using skeletal myoblasts (Menasché 2001). Since then, cell‐based therapies have been used in different trials for treating ischaemic and non‐ischaemic heart failure (Fisher 2016; Menasché 2018; Poglagen 2018; Vrtovec 2018a).

To date, several stem cell types, autologous and allogeneic, have been considered for the treatment of patients with chronic heart failure secondary to ischaemic cardiomyopathy and DCM. These include skeletal myoblasts, haematopoietic stem cells, mesenchymal stem cells, cardiac stem cells and cardiosphere‐derived cells (Menasché 2018). Haematopoietic stem cells may be collected from peripheral venous blood after a mobilisation procedure involving injection of a growth‐stimulating factor (usually granulocyte colony‐stimulating factor, G‐CSF) over the previous days to increase the number of progenitor cells in the blood and to later culture these cells ex vivo. Bone marrow‐derived stem cells may also be isolated directly from bone marrow aspiration, a procedure in which a small sample of liquid bone is aspirated with a syringe under local anaesthesia, usually from the ilium of cell therapy patients (Strauer 2002). Afterwards, mononuclear bone marrow cells are separated from other bone marrow cells by density gradient centrifugation (Assmus 2002; Erbs 2005). Stem cells are then administered to the patient using different delivery methods. The cells can be delivered through coronary arteries (Choudry 2016), coronary sinus (Patel 2015), or peripheral veins (Hare 2009). Alternatively, direct intramyocardial injection can be performed, using a surgical approach (Stamm 2010), or transendocardial (Psaltis 2010).

How the intervention might work

Clinical trials of SCT for non‐ischaemic DCM have shown promising results, such as improvement in ventricular function, functional capacity and quality of life (Frljak 2018; Poglagen 2018). Although the mechanism of action of SCT is not completely understood, two main mechanisms may promote cardiac repair. The first is that transplanted cells are engrafted into the damaged myocardium, where they generate new myocardial tissue to replace the tissue that has been irreversibly lost. The second is that SCT acts by activating endogenous repair mechanisms (Menasché 2018). This paracrine mechanism may produce stimulatory cytokines that increase vascularity, promote cardiomyocyte proliferation, limit or reduce fibrosis or activate endogenous resident stem cells (Behfar 2014). SCT may also modulate the immune system, improve endothelial function and reverse ventricular remodelling (Hare 2017).

Why it is important to do this review

Both the European Society of Cardiology (ESC) in 2016 (Ponikowski 2016), and the American Heart Association (AHA) in 2013 (Yancy 2013), refer to this therapy as an evolving therapy, and more data are needed to establish a recommendation. In the last review published by the AHA regarding diagnosis and treatment of dilated cardiomyopathy (Bozkurt 2016), cell therapy is not supported for general management.

Despite several clinical trials during the past decade, controversy remains regarding the role of SCT in DCM. For instance, SCT has not been included in major clinical practice guidelines (Bozkurt 2016; Ponikowski 2016).

Recent systematic reviews of trials published before 2015 reported that, compared with conventional therapy, bone marrow‐derived mononuclear cell therapy had a moderate effect on left ventricular ejection fraction (LVEF) and left ventricular end‐systolic volume (LVESV) in non‐ischaemic DCM (Wen 2018). An earlier review concluded the bone marrow‐derived SCT may have some effect on mortality, a mild‐to‐moderate effect on LVEF increase within six months, but no improvement in functional capacity (Lu 2016).

Since then, additional trials have been conducted using cell‐based therapies for treating non‐ischaemic heart failure (Butler 2017; Chen 2008; Frljak 2018; Hare 2017; Vrtovec 2011; Vrtovec 2013; Vrtovec 2018b; Xiao 2017). The results of these trials provide a rationale for proposing this Cochrane Review to ascertain whether this intervention provides clinical benefits in patients with DCM.

Objectives

To assess the efficacy and safety of stem cell therapy (SCT) in adults with non‐ischaemic dilated cardiomyopathy (DCM).

Methods

Criteria for considering studies for this review

Types of studies

We will include only parallel‐arm individually randomised controlled trials (RCTs). Due to the specific nature of this intervention, we do not foresee finding cluster‐ or cross‐over RCTs.

We will not restrict the study selection by publication status (i.e. whether reported as full text, as abstract only or unpublished data) or language.

Types of participants

We will include trials that have evaluated adults aged ≥ 18 years with a diagnosis of non‐ischaemic dilated cardiomyopathy (DCM) (as defined by the trial authors).

We will include trials that have evaluated both ischaemic and non‐ischaemic disease, only if the data for the participants with non‐ischaemic cardiomyopathy can be extracted separately.

Types of interventions

We will include trials that have compared:

• any type or delivery modality of stem cell therapy (SCT) versus no intervention, sham intervention or placebo (comparison number 1);

• SCT versus therapy with granulocyte colony‐stimulating factor (G‐CSF) or any other cytokine that stimulates the proliferation and differentiation of precursor cells in the bone marrow (but not comprising SCT) (comparison number 2);

• different types or delivery modalities of SCT against each other (comparison number 3).

SCT in the context of this review may consist of a variety of modalities according to cell origin (autologous or heterologous), cell collection location (bone marrow‐derived cells or peripheral blood cells), type of cells infused (bone marrow‐derived mesenchymal stromal cells, mononuclear cells, myeloid cells, lymphoid cells or mixed cells), delivery route (intracoronary, intramyocardial or transendocardial), number of cell infusions (single or repeated infusions), volume of cells infused (high or low), and the use of G‐CSF or cytokines for mobilisation of stem cells. We will take these variations into consideration when conducting the Subgroup analysis and investigation of heterogeneity.

We will accept any type of cointervention (guideline‐recommended pharmacological and device therapy or G‐CSF) when such cointervention is provided similarly to the experimental and control groups.

Although we will not restrict inclusion of trials based on specific SCT characteristics, we will consider relevant aspects related to the mode of administration of SCT in the analysis and interpretation of the results (see below in Subgroup analysis and investigation of heterogeneity).

Types of outcome measures

We will include studies that have measured any of the following outcome measures.

Primary outcomes

• All‐cause mortality

• Safety, as indicated by periprocedural complications occurring at the time of bone marrow aspiration or administration of SCT (or control)

• Safety, as documented adverse events (including tumorigenesis) within 30 days of treatment

Secondary outcomes

• Health‐related quality of life, as measured by a validated tool (e.g. Kansas City Cardiomyopathy Questionnaire, Minnesota Living with Heart Failure Questionnaire, EuroQol‐5D Questionnaire (EQ‐5D), Medical Outcome Study 36‐item Short Form Health Status Survey Questionnaire (SF‐36)

• Performance status ‐ functional class (New York Heart Association)

• Performance status ‐ exercise tolerance (6‐minute walk test)

• Rehospitalisations

• Heart failure

• Ventricular arrhythmia

• Complete atrioventricular block

• Major adverse cardiovascular events (defined as nonfatal stroke, nonfatal myocardial infarction, or cardiovascular death)

• Changes in left ventricular ejection fraction (LVEF)

• Changes in left ventricular end‐systolic volume (LVESV)

• Changes in left ventricular end‐diastolic volume (LVEDV)

• Change in blood natriuretic peptide level

If we find trials that report outcomes at several follow‐up points, we will use only the latest available time point for analysis.

Although the scope of this review is to assess the clinical effects of SCT in people with DCM, we have retained the outcome of LVEF because it is a widely reported surrogate for cardiac function. We have also included the surrogate outcomes of LVESV and LVEDV because we consider these to be more meaningful than LVEF.

We will only use one quality of life measure per study. If a study reports two or more quality of life measures, we will prioritise the measure with a specific instrument in patients with cardiomyopathy over a generic one. If the two measures were obtained with generic instruments, we will select the most widely used in the sample of studies in the review.

If a published trial does not appear to report any one of these outcomes, we will access the trial protocol and/or contact the trial authors to ascertain whether the outcomes were measured but not reported. In the review we will include relevant trials that measured these outcomes but did not report the data at all, or not in a usable format, and we will present the results in a narrative manner.

Search methods for identification of studies

Electronic searches

We will identify trials through systematic electronic searches of the following bibliographic databases.

• Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library

• MEDLINE (Ovid)

• Embase (Ovid)

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

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 adapt the preliminary search strategy for MEDLINE for use in the other databases (Appendix 1). We will apply the Cochrane sensitivity‐maximising RCT filter to MEDLINE and adapt it to Embase, but not CENTRAL (Lefebvre 2011).

We will not perform a separate search for adverse effects of interventions used for the treatment of DCM. We will consider adverse effects described in included studies only.

Searching other resources

We will also:

• handsearch the conference abstracts from relevant heart and/or stem cell conferences (the American Heart Association, the European Society of Cardiology, and the International Society of Stem Cell Research, since 2000);

• search the reference lists of all identified eligible papers and relevant systematic and/or narrative reviews as a complementary source for study identification and for validating our electronic search strategy;

• search in Epistemonikos in order to identify systematic reviews on the topic (www.epistemonikos.org), as well as all primary studies included in them by using the tool 'matrix of evidence';

• conduct a cross‐citation search in Google Scholar, using each included study as the index reference;

• when necessary, contact authors of the included studies to request additional information; and

• examine any relevant retraction statements and errata for included studies.

Data collection and analysis

Selection of studies

Once the electronic searches are performed and duplicates removed, two review authors (FV and DP) will independently screen titles and abstracts of all unique references retrieved from electronic searches for inclusion. We will code decisions as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. If there are any disagreements, a third review author will be asked to arbitrate (RD or GU). We will then retrieve the full text of all studies coded as 'retrieve' in order to assess if they meet the eligibility criteria and decide about inclusion. The same two review authors will independently evaluate the full text for inclusion. Reasons for exclusion of the ineligible studies will be coded. We will resolve any disagreement through discussion and consensus or, if required, with the participation of a third review author (RD or GU).

We will collate multiple reports of the same study so that each trial, 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 and the 'Characteristics of excluded studies' table (Liberati 2009).

Data extraction and management

We will use a standardised data collection form to extract data from each study in sufficient detail to design a comprehensive 'Characteristics of studies' table, 'Risk of bias' table, and to obtain the outcome data for the meta‐analysis. Some data will also be useful for subgroup analyses. We will pilot the data collection form before we agree with the final version of it to be used in the review.

Two review authors (FV, DP, or GU) will extract the data of each included study independently. We will resolve disagreements by consensus or by involving a third review author (RD or EM).

We will extract the following study characteristics.

• Identification of the study and bibliographic reference/s of all reports linked to the same study, as well as other secondary sources of relevant data (e.g. online supplements or trial registers)

• Elegibility criteria, as stated in the included studies

• Participants: demographic (age, sex and ethnicity), and relevant clinical data at baseline (those referred to severity of the disease and cardiac function, time from diagnosis to randomisation, body mass index, smoking status, other relevant comorbidities, family history of DCM, and previous medical and device therapy). Also, the number of people randomised, the number who dropped out, and the number analysed for each outcome

• Intervention (SCT): detailed description of SCT (including cells origin (autologous or heterologous), cell collection location (bone marrow‐derived cells or peripheral blood cells), type of cells infused (mesenchymal stromal cells, mononuclear cells, myeloid cells, lymphoid cells, or mixed), mobilisation of stem cells with cytokines (yes or no), delivery route (intracoronary, transendocardial, or intramyocardial), volume of cells administered, and number of cell infusions (single or repeated)

• Control group: detailed description of the control group, and the corresponding category of the comparison of interest (number 1: no intervention, sham or placebo; number 2: treatment with cytokines (e.g. G‐CSF), and number 3: SCT)

• Outcomes: primary and secondary outcomes planned, measured and reported, specifying the instrument of measure used and time point/s reported. Also, we will collect the outcomes reported in other secondary sources (e.g. clinical trials) in order to assess the risk of selective reporting bias.

• Methods: study design, total duration of study, study setting and country, number of centres and location, period of study

• 'Risk of bias' assessment: details on method of treatment allocation and concealment, blinding of the intervention and/or the outcome assessor, and dropouts (number, distribution and reasons) and study population of analysis.

• Data on all relevant results reported (crude number of events or rates, mean values or mean change from baseline and the corresponding standard deviation (SD), and population analysed in each study arm)

• Funding and other conflicts of interest

We will attempt to contact authors of the original trials to provide further details when necessary.

One review author (EM) will transfer data into the Review Manager file (Review Manager 2014). We will double‐check that data are entered correctly by comparing the data presented in Review Manager with the data extraction form (GU).

Assessment of risk of bias in included studies

Risk of bias in individual studies

Two review authors (FV, DP, or GU) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017). We will resolve any disagreements by discussion or by involving another review author (RD or EM).

For this purpose, we will explore the six specific domains.

• Random sequence generation

• Allocation concealment

• Blinding of participants and personnel

• Blinding of outcome assessment

• Incomplete outcome data

• Selective outcome reporting

• Other potential bias

For each trial, two review authors (FV, DP) will first independently describe the design characteristics relating to each domain and then judge the risk of bias associated with the main outcome. We will use a nominal scale for the judgement: 'low', 'high' or 'unclear' risk of bias according to the criteria described in Table 1.

Table 1.

The Cochrane tool for assessing risk of bias

Domain	Description
Random sequence generation	• Low risk: if sequence generation was achieved using computer random number generator or a random numbers table. Drawing lots, tossing a coin, shuffling cards, and throwing dice were also considered adequate if performed by an independent adjudicator. • Unclear risk: if the method of randomisation was not specified, but the trial was still presented as being randomised • High risk: if the allocation sequence was not randomised or only quasi‐randomised; we will exclude these trials
Allocation concealment	• Low risk: if the allocation of participants was performed by a central independent unit, on‐site locked computer, identical‐looking numbered sealed envelopes, syringes prepared by an independent investigator • Uncertain risk: if the trial was classified as randomised but the allocation concealment process was not described • High risk: if the allocation sequence was familiar to the investigators who assigned participants
Blinding of participants and personnel	• Low risk: if the participants and the personnel were blinded to intervention allocation and this was described • Uncertain risk: if the procedure of blinding was insufficiently described or not described at all • High risk: if blinding of participants and the personnel was not performed
Blinding of outcome assessment	• Low risk of bias: if it was mentioned that outcome assessors were blinded and this was described • Uncertain risk of bias: if it was not mentioned if the outcome assessors in the trial were blinded, or the extent of blinding was insufficiently described • High risk of bias: if no blinding or incomplete blinding of outcome assessors was performed
Incomplete outcome data	• Low risk of bias: if missing data were unlikely to make treatment effects depart from plausible values. This could either be: 1) there were no dropouts or withdrawals for all outcomes, or 2) the numbers and reasons for the withdrawals and dropouts for all outcomes were clearly stated and could be described as being similar in both groups. Generally, the trial is judged at low risk of bias due to incomplete outcome data if dropouts are less than 5%. However, the 5% cut‐off is not definitive. • Uncertain risk of bias: if there was insufficient information to assess whether missing data were likely to induce bias on the results • High risk of bias: if the results were likely to be biased due to missing data either because the pattern of dropouts could be described as being different in the two intervention groups or the trial used improper methods in dealing with the missing data (e.g. last observation carried forward)
Selective outcome reporting	• Low risk of bias: if a protocol was published before or at the time the trial was begun and the outcomes specified in the protocol were reported on. If there is no protocol or the protocol was published after the trial has begun, reporting of all‐cause mortality and periprocedural complications (the 2 primary outcomes) will grant the trial a grade of low risk of bias. • Uncertain risk of bias: if no protocol was published and the two primary outcomes were not reported on • High risk of bias: if the outcomes in the protocol were not reported on
Other risks of bias	• Low risk of bias: if the trial appears to be free of other components (for example, academic bias or for‐profit bias) that could put it at risk of bias • Unclear risk of bias: if the trial may or may not be free of other components that could put it at risk of bias • High risk of bias: if there are other factors in the trial that could put it at risk of bias (for example, authors have conducted trials on the same topic, for‐profit bias etc.)

The table was adapted from Table 8.5.d: Criteria for judging risk of bias in the 'Risk of bias' assessment tool, in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017).

We will contact the principal investigator or study sponsor in order to obtain or clarify key study features for a proper 'Risk of bias' assessment.

Overall risk of bias

• Low risk of bias: we will classify the outcome result at overall 'low risk of bias' only if we classify all of the bias domains (described above) at low risk of bias. For objective outcomes, e.g. mortality, we will consider whether blinding is of relevance, and may still categorise this at overall low risk of bias if a lack of blinding is unlikely to introduce bias.

• High risk of bias: we will classify the outcome result at 'high risk of bias' if we classify any of the bias domains (described above) at 'unclear' or 'high risk of bias'.

We will generate a 'Risk of bias' table specifying all these judgements, and provide a detailed justification for each judgement so that it may be transparent and reproducible. Where information on risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the 'Risk of bias' table.

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

Assessment of bias in conducting the systematic review

We will conduct the review according to this published protocol and report any deviations from it in the 'Differences between protocol and review' section of the systematic review.

Measures of treatment effect

We will express dichotomous data for each arm in a particular study as a proportion or risk and the treatment effect as a risk ratio (RR) with 95% confidence intervals (CIs), calculated using Mantel‐Haenszel methods. We will express continuous data for each arm in a particular study as a mean and SD, and the treatment effect as the mean difference (MD) if outcomes are measured in the same way across trials. For outcomes measured using different methods, we will combine the treatment effect data and analyse them using the standardised mean difference (SMD).

We will analyse continuous outcomes as mean change from baseline. For studies that only report baseline and endpoint data, when possible we will calculate the SD of the mean change from baseline based on reported CIs or P values, and use these values in the analysis. Studies with insufficient information to calculate the SD (e.g. studies that only report endpoint mean values), will be presented separately, as well as in combined analyses (in this latter case assuming the differences in mean final values will on average be the same as the differences in mean change scores), as suggested in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

Unit of analysis issues

We will only include parallel‐group individually randomised clinical trials.

Where multiple trial intervention groups are reported in a single trial, we will include only the relevant groups. If two relevant comparisons are included in the same meta‐analysis, we will halve the control group to avoid double‐counting (Deeks 2017).

Dealing with missing data

We will contact the principal investigator or study sponsor in order to obtain missing numerical outcome data where possible (e.g. when a study is identified as abstract only).

Where possible, we will use the RevMan calculator (RevMan 2014) to calculate missing SDs using other data from the trial, such as CIs. 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, using the software SAMURAI (Kim 2014), available in R software (R 2017).

We will not impute missing values for any dichotomous nor continuous outcomes in our primary analysis.

To assess the potential impact of the missing data for dichotomous outcomes, we will perform the following sensitivity analyses when assessing each dichotomous outcome.

• 'Best‐worst‐case' scenario: we will assume that all participants lost to follow‐up in the experimental group had a favourable result in each of the outcomes, and all those participants lost to follow‐up in the control group had a negative result.

• 'Worst‐best‐case' scenario: we will assume that all participants lost to follow‐up in the experimental group had a negative result in each of the outcomes, and that all those participants lost to follow‐up in the control group had a favourable result.

To assess the potential impact of missing SDs for continuous outcomes, we will perform the following sensitivity analysis.

• Where SDs are missing and it is not possible to calculate them, we will impute SDs from trials with similar populations and low risk of bias. If we find no such trials, we will impute SDs from trials with a similar population. As the final option, we will impute SDs from all trials.

Assessment of heterogeneity

We will primarily inspect forest plots visually to consider the direction and magnitude of effects and the degree of overlap between CIs. We will secondly consider the P value from the Chi² test (threshold P < 0.10) to address the presence of statistical heterogeneity. We will also use the I² statistic to quantify statistical heterogeneity not attributable to chance among the trials in each analysis, but acknowledge that there is substantial uncertainty in the value of I² when there is only a small number of studies. We will follow the recommendations for thresholds in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017):

• 0% to 40%: might not be important;

• 30% to 60%: may represent moderate heterogeneity;

• 50% to 90% may represent substantial heterogeneity;

• 75% to 100%: may represent considerable heterogeneity.

In case we identify substantial and considerable heterogeneity, we will report it and explore possible causes by prespecified subgroup analysis. Ultimately, we may decide that a meta‐analysis should be avoided (Deeks 2017).

Assessment of reporting biases

If we are able to pool more than 10 trials in the meta‐analyses, we will create and examine a funnel plot to explore possible small study biases for the primary outcomes. For dichotomous outcomes, we will test asymmetry with the Harbord test (Harbord 2006). For continuous outcomes, we will use the regression asymmetry test (Egger 1997).

Data synthesis

We will undertake meta‐analyses only where this is meaningful (i.e. if the treatments, participants and the underlying clinical question are similar enough for pooling to make sense), and according to the recommendations stated in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017). We will use the Cochrane statistical software Review Manager 5 to analyse data (Review Manager 2014).

We will assess the intervention effects with both random‐effects meta‐analyses (DerSimonian 1986), and fixed‐effect meta‐analyses (DeMets 1987). We will use the more conservative point estimate of the two. If the two estimates are similar, we will use the estimate with the widest CI.

'Summary of findings' table

We will create a 'Summary of findings' table for each planned comparison, using the following outcomes included in the review: all‐cause mortality, periprocedural complications, adverse events up to 30 days, health‐related quality of life, performance status (functional class), performance status (exercise tolerance), major adverse cardiovascular events and ventricular arrhythmia. For each outcome, we will only present data at the longest follow‐up that is available for each study.

We will use the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of a body of evidence as it relates to the studies which contribute data to the meta‐analyses for the prespecified outcomes. We will use methods and recommendations described in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2017), using GRADEpro software (GRADEpro GDT 2015).

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.

Judgements about evidence quality will be made by two review authors (GR and GU) working independently, with disagreements resolved by discussion or involving a third review author (RD or EM). Judgements will be justified, documented and incorporated into reporting of results for each outcome.

We plan to extract study data, format our comparisons in data tables and prepare a 'Summary of findings' table before writing the results and conclusions of our review. A template of a 'Summary of findings' table is included as Table 2.

Table 2.

'Summary of findings' table ‐ draft

Stem cell therapy versus no intervention, sham intervention or placebo
Patient or population: adults (≥ 18 years of age) with a diagnosis of non‐ischaemic dilated cardiomyopathy Setting: hospital Intervention: stem cell therapy Comparison: no intervention, sham intervention or placebo
Outcomes	Anticipated absolute effects* (95% CI)		Relative effect (95% CI)	№ of participants (studies)	Certainty of the evidence (GRADE)	Comments
	Risk with control	Risk with treatment
All‐cause mortality
Safety (periprocedural complications)
Safety (adverse events) within 30 days of treatment
Health‐related quality of life
Performance status (functional class)
Performance status (exercise tolerance)
Major adverse cardiovascular events
Ventricular arrhythmia
*The risk in the intervention group (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). CI: confidence interval; RR: risk ratio; OR: odds ratio;
GRADE Working Group grades of evidence High certainty: we are very confident that the true effect lies close to that of the estimate of the effect. Moderate certainty: 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 certainty: our confidence in the effect estimate is limited; the true effect may be substantially different from the estimate of the effect. Very low certainty: we have very little confidence in the effect estimate; the true effect is likely to be substantially different from the estimate of effect.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following exploratory subgroup analyses for each outcome.

• Comparison of the effects between trials with different cell origin (autologous versus heterologous)

• Comparison of the effects between trials with different collection location (bone marrow‐derived cells versus peripheral blood cells versus other

• Comparison of the effects between trials with different type of cells infused (bone marrow‐derived mesenchymal stromal cells, mononuclear cells, myeloid cells, lymphoid cells or mixed cells)

• Comparison of the effects between trials with/without mobilisation of stem cells with use of G‐CSF or cytokines

• Comparison of the effects between trials with different delivery route (intracoronary, intramyocardial or transendocardial)

• Comparison of the effects between trials with different number of cell infusions (single versus repeated infusions)

• Comparison of the effects between trials with different volume of cells infused (high versus low)

• Comparison of the effects between trials with different baseline cardiac function (mean baseline LVEF < 30% versus 30% to 40% versus > 40%)

• Comparison of the effects between trials with different follow‐up durations (up to 12 months versus > 12 months)

• Comparison of the effects according to the body mass index (normal weight versus overweight versus obese)

• Comparison of the effects according to smoking status (currently or ex‐smoker versus never smoker)

We will use the formal test for subgroup differences in Review Manager (Review Manager 2014), and base our interpretation on this.

We will perform subgroup analysis, when possible, only for the first two planned comparisons.

Other posthoc subgroup analyses might be warranted if we identify unexpected clinical or statistical heterogeneity during the analysis of the review results.

Sensitivity analysis

We will include all trials in our analyses and conduct a sensitivity analysis excluding trials with high risk of bias. If the results are similar, we will base our primary conclusions on the overall analysis. If they differ, we will base our primary conclusions on trials at low risk of bias.

We will also perform a set of sensitivity analyses to explore the impact on imputing missing data.

Reaching conclusions

We will base our conclusions only on findings from the quantitative or narrative synthesis of included studies for this review. We will avoid making recommendations for practice and our implications for research will suggest priorities for future research and outline what the remaining uncertainties are in the area.

Appendices

Appendix 1. Preliminary MEDLINE (OVID) search strategy

1. exp "Cell‐ and Tissue‐Based Therapy"/ (264867)

2. exp Stem Cells/ (193476)

3. exp bone marrow cells/ (175306)

4. hematopoietic.tw. (85675)

5. haematopoietic.tw. (9393)

6. hemopoietic.tw. (8537)

7. haemopoietic.tw. (4033)

8. ((stem or progenitor or precursor or mesenchymal or stromal) adj2 (cell or cells or marrow)).tw. (329766)

9. or/1‐8 (705087)

10. Cardiomyopathy, Dilated/ (14921)

11. (dilat* adj2 cardiomyop*).tw. (16670)

12. (congestiv* adj2 cardiomyop*).tw. (1313)

13. (familial idiopath* adj2 cardiomyop*).tw. (16)

14. DCM.tw. (6453)

15. or/10‐14 (25303)

16. 9 and 15 (519)

17. randomized controlled trial.pt. (474740)

18. controlled clinical trial.pt. (92739)

19. randomized.ab. (432962)

20. placebo.ab. (194801)

21. drug therapy.fs. (2075064)

22. randomly.ab. (304454)

23. trial.ab. (452151)

24. groups.ab. (1874672)

25. 17 or 18 or 19 or 20 or 21 or 22 or 23 or 24 (4360826)

26. exp animals/ not humans.sh. (4534465)

27. 25 not 26 (3770673)

28. 16 and 27 (95)

Contributions of authors

RD, EM and GU drafted the protocol. All the authors read and approved the final manuscript.

Sources of support

Internal sources

• No sources of support supplied

External sources

• This project was supported by the National Institute for Health Research, 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, UK.

• This project was supported by the CONICYT (grant num. MEC80170060), Chile.

Declarations of interest

The performance of this review is free of any real or perceived bias introduced by receipt of any benefit in cash or kind, or any subsidy derived from any source that may have or be perceived to have an interest in the outcomes of the review.

RD: none known

JGFC: Professor Cleland received payment as a member of an advisory board for TEVA/Cephalon in 2011/12 leading to a trial of stem cell therapy for heart failure in which he was not subsequently involved. He has had no contact with TEVA/Cephalon in the last six years. He has consulted widely with other healthcare companies but not on the topic of stem cells.

GU: has received honoraria for educational activities (workshops) from several laboratories.

DP: none known

FV: none known

SB: I have co‐authored a paper based on a grant from the European Commission that ended in 2014 (Kim 2014). The methodology of the paper is likely to be used for the sensitivity analyses in this Cochrane Review.

GR: none known

EM: none known

New