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The Cochrane Database of Systematic Reviews logoLink to The Cochrane Database of Systematic Reviews
. 2019 Apr 23;2019(4):CD012113. doi: 10.1002/14651858.CD012113.pub2

Aspirin dosage for the prevention of graft occlusion in people undergoing coronary surgery

Fares Alahdab 1,✉, Mhd Luay Jazayerli 2, Omar Alhalabi 3, Somar Hasan 4, Mahmoud Mallak 5, Mohamad Alkhouli 6, Qusay Haydour 7, M Hassan Murad 8
PMCID: PMC6478429

Abstract

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

To evaluate the use of different dose regimens of aspirin to prevent graft occlusion in people who have undergone coronary artery bypass grafting.

Background

Description of the condition

Coronary artery bypass graft (CABG) surgery has been the standard treatment approach of advanced coronary artery disease (CAD). In one observational study, 18‐month rates of death, myocardial infarction (MI) and repeated revascularisation were reduced in people with multi‐vessel coronary disease treated with CABG compared with people treated using drug‐eluting stents (Hannan 2008). In additional, one randomised controlled trial (RCT) showed that the 12‐month rates of major cardiac or cerebrovascular events were significantly lower in people with severe CAD receiving CABG compared with percutaneous coronary intervention (PCI) (Serruys 2009). Among people with multi‐vessel CAD, the rate of major cardiovascular events was higher in people who had PCI than in people who had CABG (Park 2015). CABG has also been shown to be more efficacious than PCI with first‐generation drug‐eluting stents in people with left main and multi‐vessel CAD (Al Ali 2014). The 2011 ACC/AHA (American College of Cardiology/American Heart Association) guidelines state that CABG is the preferred treatment for disease of the left main coronary artery (LMCA), disease of all three coronary vessels (left anterior descending (LAD), left circumflex artery (LCX) and right coronary artery (RCA)), and diffuse disease not amenable to treatment with a PCI (Hillis 2011). It is also the preferred approach for people at high‐risk, such as people with severe ventricular dysfunction (i.e. low ejection fraction), or diabetes mellitus (Hillis 2011). CABGs are commonly performed utilising the combination of a single arterial graft (left internal mammary artery (LIMA)) and multiple saphenous vein grafts (SVG) (Keogh 2002). Although CABG utilisation rate decreased in the USA between 2001 and 2008, there still are 1081 CABGs performed per million adults per year (2007 to 2008 figures) (Epstein 2011). At this point in time in medical practice, the main focus is to improve the results of CABG and the long‐term survival of people undergoing coronary surgery.

The long‐term success of CABG surgery largely relies on the persistent patency of the graft conduits. SVGs have the benefits of being abundant and easy to harvest, but their long‐term patency compared to LIMA is poor. For vein grafts generally, 15% to 30% are occluded within one year after CABG, and about 50% of these occlusions happen in the first two weeks (Cooper 1996). However, after the first year post‐CABG, the annual occlusion rate is 2% to 5%. Ten years after the surgery, approximately one‐third of the vein grafts that had been patent at one year remain patent and another third become occluded (Bourassa 1994). Other studies have shown that 12% of vein grafts are occluded within one year, 25% within five years, and 50% within 12 years after CABG (FitzGibbon 1996), and even more studies reported an incidence of one or more total SVG occlusions to be as high as 41% at one year after on‐pump CABG (Alexander 2005; Gluckman 2011; Goldman 2004; Halabi 2005; Khot 2004; Shroyer 2009; Widimsky 2004). This explains why 3% of participants need a repeat operation within five years, 10% within 10 years, and 25% within 20 years (Cohn 2008). The occlusive process is associated with the angiographic and histological findings of acute thrombosis and intimal hyperplasia within the first year after CABG and the onset and progression of atherosclerosis beyond three to five years. These three mechanisms are the leading causes of vein graft failures after CABG (Harskamp 2013). Hybrid revascularisation (LIMA to LAD, and PCI to the other occluded coronaries) is thought to be the solution to the problem of high rates of vein graft failure (Harskamp 2015; Panoulas 2015). However, the utilisation rates have been very disappointing and vein grafts are still used for the majority of people (Shannon 2012). Data on the results of hybrid procedures have been inconsistent, unfortunately (Modrau 2015). This highlights the importance of continuing to search for the optimal strategy to improve vein graft latency.

Description of the intervention

Lack of aspirin (acetylsalicylic acid) prescribed at hospital discharge (discharge aspirin) was the strongest independent correlate of long‐term mortality after CABG in the land mark SYNTAX trial (Farooq 2012). Platelet inhibition represents a therapeutic mainstay in treating people with CABG, and they routinely receive aspirin as a standard treatment for preventing occlusion and preserving bypass graft surgery benefits (Gavaghan 1991), and continue it indefinitely (Hillis 2011). Furthermore, early post‐operative aspirin within six hours following CABG has been reported to be the best approach for prevention of vein graft occlusion (Gukop 2014). Platelet inhibition is associated with a reduced risk of death, reduced ischaemic complications and improved graft patency (Karzai 2003; Mangano 2002; Patel 2009; Stein 2004). This desired effect of aspirin diminishes the later it is administered (Gukop 2014). Aspirin is the drug of choice for the prevention of SVG closure in the short term and is recommended for indefinite use following the procedure due to its benefit in secondary prevention of death and cardiac events in people with CAD (Hillis 2011). Despite this benefit, its use for longer than one year following CABG does not seem to improve vein graft patency (Goldman 1994).

The antithrombotic effect of aspirin is mediated by inhibition of blood platelets function. The best characterised mechanism of action of aspirin occurs through permanent inactivation of the cyclo‐oxygenase (COX) activity of prostaglandin H (PGH) synthase 1 and synthase 2, also referred to as COX‐1 and COX‐2, respectively (Roth 1975). The balance between production of prostaglandin I2 (an inhibitor of aggregation, generated by the vascular endothelium) and thromboxane (TX) (a stimulant of aggregation, generated by platelets) is thus altered; endothelium can synthesise more of the COX enzyme but platelets cannot (Rang 2003).

In people with acute coronary syndrome treated with aspirin, major bleeding increased in a dose‐related pattern with 1.9% at low doses (less than 100 mg daily), 2.8% at medium doses (100 to 200 mg daily) and 3.7% at high doses (greater than 200 mg daily) (Peters 2003). At low‐dose aspirin, the main adverse effects are gastric irritation and ulceration. The gastritis that occurs with aspirin may be due to irritation of the gastric mucosa by the undissolved tablet, absorption in the stomach of non‐ionised salicylate or inhibition of the production of protective prostaglandins (Katzung 2001). Aspirin is effective in reducing further events in people with coronary heart disease; however, evidence is not conclusive as to which dose is optimal (Gukop 2014; Zimmermann 2008).

How the intervention might work

Despite aspirin's therapeutic effect, early graft loss due to thrombosis and the late atherosclerosis‐driven occlusion remain concerns. The rate of complete graft occlusion after one year is 8.2% with radial artery grafts and 13.6% with SVGs (Desai 2004), and the mechanisms of this failure involve platelet activation and atherothrombosis (i.e. the process of graft occlusion after CABG starts with thrombi formation at the sites of intimal disruption and gradually develops into atherosclerosis). Intimal hyperplasia also develops in SVGs after CABG (Motwani 1998).

Significant risk factors for SVG thrombosis within six months of CABG surgery in people taking post‐operative aspirin include small target vessel diameter, female gender and low mean graft blood flow (McLean 2011). The internal mammary artery grafts had the highest early patency rate among the coronary bypass grafts.

Post‐operative aspirin improves survival in participants undergoing CABG. Aspirin and other antiplatelet agents have been proven to be of variable benefit following bypass practices. For example, ticlopidine plus aspirin after coronary stenting were effective in reducing the risk of revascularisation, non‐fatal MI and bleeding complications when compared with other oral anticoagulants (Schomig 1997). Antiplatelet therapy with aspirin had a slight beneficial effect on the patency of peripheral bypass grafts (Brown 2008). However, the debate on dosages of aspirin continues. Some studies showed that there is lack of additional benefit with high‐dose aspirin but this was accompanied with an increased risk of bleeding (Mehta 2010; Peters 2003). Residual platelet activity was lower in participants who received aspirin 325 mg compared to participants who received aspirin 100 mg (Brambilla 2010). Moreover, a single dose of aspirin 325 mg on the first post‐operative day may have a greater inhibitory effect on collagen‐induced aggregation than a single dose of aspirin 100 mg (Cornelissen 2006).

Why it is important to do this review

The 2011 ACC/AHA guidelines recommend that every person receives daily aspirin therapy after CABG (Class I indication) (Hillis 2011). The 2012 American College of Chest Physicians (ACCP) guidelines on the primary and secondary prevention of cardiovascular disease also state that people who undergo CABG should be started on aspirin and it should be continued indefinitely (Vandvik 2012). Several studies assessed whether early treatment with aspirin inhibits platelet aggregation, has an effect on graft patency, or improves survival after coronary bypass surgery. Many of these studies have showed that early use of aspirin after CABG reduces the risk of death and ischaemic complications (Antiplatelet Trialists' Collaboration 1994; Fremes 1993; Henderson 1989; Mangano 2002). However, the guideline and many of the studies took no account of the wide variation in aspirin doses (from 75 to 325 mg). As a result, low‐dose aspirin (75 to 150 mg) is usually prescribed despite the lack of direct comparison with medium‐ or high‐dose regimens (Lim 2003). The uncertainty of the optimum dose of aspirin after CABG is the main reason why this review is important.

Objectives

To evaluate the use of different dose regimens of aspirin to prevent graft occlusion in people who have undergone coronary artery bypass grafting.

Methods

Criteria for considering studies for this review

Types of studies

We will include all RCTs (irrespective of language or sample size) comparing different dosages of aspirin for the purpose of maintaining graft patency in people who have undergone CABG surgery. We will exclude all quasi‐randomised studies, such as those allocating using alternate days of the week or surname of the participant, as they are not truly randomised and are more prone to bias. We will not include cross‐over trials. We will also exclude trials that did not study aspirin as the sole therapy or trials not including a comparison group.

A given participant population will only be used once: if the same population appeared in other trials, we will include the article that provides the most complete follow‐up data. We will also exclude studies where one or more of the participant groups received another treatment, such as clopidogrel, because it would be difficult to adjust for the effects of the additional intervention.

Types of participants

People who have undergone coronary artery surgery (both on‐ and off‐pump, and including emergency and elective procedures) and have been placed on aspirin therapy after surgery. We will include all trials of participants aged 18 years and older, of either gender and in any clinical setting.

Types of interventions

We will include all studies comparing different dosages of aspirin in participants who have undergone coronary surgery.

Types of outcome measures

We will analyse outcomes for different lengths of follow‐up: up to three months, six months, one year, five years and 10 years, if possible.

Primary outcomes

  • Short‐term post‐operative cardiovascular‐related mortality (i.e. within 30 days of the operation).

  • Short‐term post‐operative all‐cause mortality (i.e. within 30 days of the operation).

  • Aspirin adverse effects:

    • minor adverse effects;

    • major adverse effects (such as local gastric toxicity, acute renal failure).

Secondary outcomes

  • Failed on first CABG attempt.

  • Need for coronary intervention.

  • Recurrence of cardiovascular events (e.g. MI, stable or unstable angina).

  • Heart failure.

  • Health‐related quality of life (as defined by the individual trials).

  • Health‐related costs.

Search methods for identification of studies

Electronic searches

We will search the following electronic databases: the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE (Ovid), EMBASE (Ovid) and Web of Science (Thomson Reuters) from their inception to the date of the review.

We will design searches in accordance with the Cochrane Heart Group methods and guidance. We will use medical subject headings (MeSH) or equivalent and text word terms and will impose no language restrictions. Appendix 1 shows the search strategy for MEDLINE, which we will tailor to individual databases.

Searching other resources

We will check reference lists of reviews and retrieved articles for additional studies. We will search the Clinical trials.gov (www.clinicaltrials.gov) and the World Health Organization (WHO) International Clinical Trials Registry platform (ICTRP) (apps.who.int/trialsearch/) for ongoing trials. We will contact experts in the field for unpublished and ongoing trials and we will contact trial authors where necessary for any additional information.

Data collection and analysis

We will perform the review and meta‐analyses following the recommendations of Cochrane (Higgins 2011a). We will perform the analyses using Review Manager 5 (RevMan 2014).

Selection of studies

Two authors will independently inspect citations from the searches and identify relevant abstracts. A third author will inspect a random 20% sample of these citations to ensure reliability. Two authors will obtain and inspect full reports of the abstracts that meet the review criteria, plus citations that authors disagree on. A third author will inspect a random 20% of these full reports in order to ensure reliable selection. Where it is not possible to resolve a disagreement by discussion, we will attempt to contact the authors of the study for clarification (Higgins 2011b).

Data extraction and management

Two authors will independently extract data from relevant studies. We will discuss and document any disagreements. With remaining disagreements, a third author will help clarify issues and we will document the final decisions. We will extract data presented only in graphs and figures whenever possible, but will only include them if two authors independently had the same result. If studies are multi‐centre, where possible, we will extract data relevant to each component centre separately.

We will use a standardised template of a data collection form to extract data on methods, participants, interventions and outcomes.

Assessment of risk of bias in included studies

Working independently, two authors (MM and LJ) will assess methodological risk of bias of included studies for adequacy of sequence generation, allocation concealment, blinding (participants, personnel and outcome), drop‐out rates (incomplete outcome data), analysis of intention to treat (ITT), selective outcome reporting and other biases using the tool described in the Cochrane Handbook for Systematic Reviews of Interventions (Tables 8.5a‐c) (Higgins 2011a).

We will assess and categorise the risk of bias in each domain and overall bias as:

  • low risk of bias: plausible bias unlikely to seriously alter the results;

  • high risk of bias: plausible bias that seriously weakens confidence in the results;

  • unclear risk of bias: plausible bias that raises some doubt about the results.

If any disagreement arises, we will make the final decision by consensus, with the involvement of another author. We will contact authors of the studies if details about randomisation or other characteristics of the trial are missing. We will report non‐concurrence in quality assessment, but if disputes arise as to which category a trial is to be allocated, we will obtain resolution by discussion.

Measures of treatment effect

For binary outcomes (e.g. MI or no MI at follow‐up), we will calculate a standard estimation of the random‐effects (DerSimonian 1986) risk ratio (RR) and its 95% confidence interval (CI). It has been shown that RRs are more intuitive than odds ratios (Boissel 1999), and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). This misinterpretation then leads to an overestimate of the impression of the effect. Where possible, we will make efforts to convert outcome measures to dichotomous data. This can be done by identifying cut‐off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. We will assume that if there had been a 50% reduction in a scale‐derived score, this could be considered as a clinically significant response. If data based on these thresholds are not available, we will use the primary cut‐off presented by the original authors.

We will contact the authors of all the trials wherever we find missing data.

Unit of analysis issues

We do not anticipate finding cluster trials in this review. Studies increasingly employ 'cluster randomisations' (such as randomisations by clinical or practice) but analysis and pooling of clustered data poses problems. For example, authors often fail to account for intra‐class correlation in clustered studies, leading to a 'unit of analysis' error (Divine 1992), whereby P values are spuriously low, CIs unduly narrow and statistical significance overestimated. This causes type I errors (Bland 1997; Gulliford 1999).

If results from trials did not adjust for clustering, we will attempt to adjust the results for clustering by multiplying the standard errors of the effect estimates (RR or mean difference, ignoring clustering) by the square root of the design effect. The design effect is calculated as DEff = 1 + (M ‐ 1)ICC, where M is the mean cluster size and ICC is the intra‐cluster coefficient (Higgins 2011b). If an ICC is not available from the trial, we will use other sources to impute ICCs (Campbell 2000).

Where clustering is incorporated into the analysis of primary studies, we will present these data as if from a non‐cluster randomised study, but adjusted for the clustering effect. If a cluster study is appropriately analysed taking into account intra‐class correlation co‐efficient and relevant data documented in the report, synthesis with parallel group randomised trials is possible using the generic inverse variance technique. This is where the natural logarithm of the effect estimate (and standard errors) for all included trials for that outcome is calculated and entered into Review Manager 5 along with the log of the effect estimate (and standard errors) from the cluster randomised trial(s) (RevMan 2014).

Dealing with missing data

At some degree of loss of follow‐up, data must lose credibility (Xia 2007). The loss to follow‐up in randomised trials is often considerable calling into question the validity of the results. Nevertheless, it is unclear which degree of attrition leads to a high degree of bias. We will not exclude trials from outcomes on the basis of the percentage of participants completing them. However, we will use the Cochrane 'Risk of bias' tool to indicate potential bias when more than 25% of the participants left the studies prematurely, when the reasons for attrition differed between the intervention and control group, and when no appropriate imputation strategies were applied.

We will present data on a 'once‐randomised‐always‐analysed' basis, assuming an ITT analysis. If the authors applied such a strategy, we will use their results. If the authors presented only the results of the per‐protocol or completer population, we will assume that those participants lost to follow‐up would have had the same percentage of events as participants who remained in the study.

We will not have continuous data because our outcomes will be binary.

Assessment of heterogeneity

We will consider all included studies without any comparison data to judge clinical and methodological heterogeneity. We will inspect all studies for clearly outlying situations or people that we had not predicted and discuss them fully.

We will visually inspect forest plots to identify trials with non‐overlapping CIs to suggest the possibility of statistical heterogeneity.

We will investigate heterogeneity between studies by considering the I2 statistic and the Chi2 P value. The I2 statistic provides an estimate of the percentage of inconsistency thought to be due to chance (Higgins 2003). The importance of the observed value of the I2 statistic depends on the magnitude and direction of effects, and the strength of evidence for heterogeneity (e.g. P value from Chi2 test, or a CI for the I2 statistic).

We will interpret an I2 statistic estimate of 50% or greater accompanied by a statistically significant Chi2 statistic as evidence of substantial levels of heterogeneity (Section 9.5.2; Higgins 2003), and will explore reasons for heterogeneity. If inconsistency is high and we find clear reasons for this, we will present data separately.

Assessment of reporting biases

If the search identifies 10 or more studies, we will enter the data for each outcome into a funnel plot (trial effect versus trial size) in an attempt to investigate the likelihood of overt publication bias. We will test for funnel plot asymmetry only for outcomes where there were 10 or more studies and if the studies were not of similar sizes, as recommended in Section 10.4.3.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). If we find asymmetry, we will discuss this to consider reasons other than publication bias, for example, selection bias, reporting bias, data irregularities, true heterogeneity and artefact (Sterne 2001). We will use the statistical test by Egger to assess funnel plot asymmetry formally, and supplemented this by visual inspection of the forest plot to differentiate small‐study effects from other reasons for funnel plot asymmetry (Egger 1997).

Data synthesis

We understand that there is no closed argument for preference for use of fixed‐effect or random‐effects models. The random‐effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This often seems to be true and the random‐effects model takes into account differences between studies even if there is no statistically significant heterogeneity. However, there is a disadvantage to the random‐effects model since it puts added weight onto small studies, which often are the most biased ones (Sterne 2011). Depending on the direction of effect, these studies can either inflate or deflate the effect size.

We will analyse data using a random‐effects model and a fixed‐effect model. In case of discrepancy between the two models, we will report both results. Otherwise, we will only report results from the random‐effects model. We will analyse data according to the ITT principle and present them as RR and risk difference with 95% CIs.

Summary of findings table

We will create a 'Summary of findings' table using the following outcomes: mortality (all‐cause and cardiovascular related), failed on first CABG event, PCI, recurrence of cardiovascular events, heart failure and adverse events of aspirin. 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 that contribute data to the meta‐analyses for the pre‐specified outcomes. We will use methods and recommendations described in Section 8.5 and Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) using GRADEpro software. We will justify all decisions to downgrade or upgrade the quality of studies using footnotes and we will make comments to aid the reader's understanding of the review where necessary.

Subgroup analysis and investigation of heterogeneity

Subgroup analyses will be performed to assess the benefit in particular pre‐defined subgroups.

Subgroup analyses

If case of sufficient number of studies (i.e. three RCTs or more), we will try to present data for the following subgroups:

  • people who have undergone CABG with similar baseline risk factors;

  • emergency versus non‐emergency cardiac surgery;

  • venous versus arterial grafts;

  • for primary outcomes, if data exist, these will be reported as subgroup analyses.

Investigation of heterogeneity

If inconsistency is high, we will report this. First, we will investigate whether data had been entered correctly. Second, if data are correct, we will visually inspect the graph and successively remove studies outside of the company of the rest to see if homogeneity is restored. Should this occur with no more than 10% of the data being excluded, we will present the data. If not, we will not pool data and will discuss the issues.

Sensitivity analysis

These analyses will only apply to the primary outcomes. We are conscious of the risk of finding significant results because of the play of chance secondary to multiple analyses.

Risk of bias

We will analyse the effects of excluding trials that we judge to be at high risk of bias across one or more of the domains of randomisation (implied as randomised with no further details available), allocation concealment, blinding and outcome reporting for the meta‐analysis of the primary outcome. If the exclusion of trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then we will include data from these trials in the analysis.

Imputed values

We will also undertake a sensitivity analysis to assess the effects of including data from trials where we used imputed values. If substantial differences are noted in the direction or precision of effect estimates, we will not pool data but present them separately.

Fixed and random effects

We will synthesise data for the primary outcomes using a random‐effects model to evaluate whether the greater weights assigned to smaller trials altered the significance of the results, compared with the less evenly distributed weights in the fixed‐effect model.

Unpublished studies

We will analyse data from published studies (those with a report in peer‐reviewed journals) and compare these findings with outcomes from trials that have not yet appeared in full report in peer‐reviewed journals. We propose to comment of these findings but not take action on them.

Industry funding

We will analyse the primary outcomes from trials funded or supported by industry and compare these data with those from more independent studies. We propose to comment on these findings but not exclude or include studies because of them.

Appendices

Appendix 1. MEDLINE (Ovid) search strategy

MEDLINE (Ovid)

1. Aspirin/

2. aspirin*.tw.

3. (acetylsalicylic adj2 acid*).tw.

4. dispril*.tw.

5. polopiryna.tw.

6. zorprin.tw.

7. polopirin.tw.

8. colfarit.tw.

9. aloxiprimum.tw.

10. micristin.tw.

11. easprin.tw.

12. magnecyl.tw.

13. solprin.tw.

14. ecotrin.tw.

15. "2‐(acetyloxy)benzoic acid*".tw.

16. endosprin.tw.

17. acylpyrin.tw.

18. solupsan.tw.

19. acetysal.tw.

20. or/1‐19

21. exp Coronary Artery Bypass/

22. artery bypass*.tw.

23. aortocoronary bypass*.tw.

24. CABG.tw.

25. (coronary adj5 bypass*).tw.

26. ((coronary or heart or myocard*) adj5 revasculari*).tw.

27. (coronary adj5 surg*).tw.

28. Graft Occlusion, Vascular/

29. (graft adj2 occlu*).tw.

30. (graft adj2 restenosis).tw.

31. or/21‐30

32. 20 and 31

33. randomized controlled trial.pt.

34. controlled clinical trial.pt.

35. randomized.ab.

36. placebo.ab.

37. drug therapy.fs.

38. randomly.ab.

39. trial.ab.

40. groups.ab.

41. 33 or 34 or 35 or 36 or 37 or 38 or 39 or 40

42. exp animals/ not humans.sh.

43. 41 not 42

44. 32 and 43

What's new

Date Event Description
23 April 2019 Amended This protocol has been withdrawn as the author team is unable to progress to the final review stage.
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Contributions of authors

FA was responsible for the methodology, and contributed to drafting and critical review of the manuscript.

OA, SH, MLJ and MM contributed to drafting and critical review of the manuscript.

FA, OA and MLJ contributed to the clinical context and expertise.

Sources of support

Internal sources

  • No funding or other support received., Other.

    No funding or other support received.

External sources

  • No funding or other support received., Other.

    No funding or other support received.

Declarations of interest

FA: None known.

MLJ: None known.

OA: None known.

SH: None known.

MM: None known.

MA: None known.

QH: None known.

MHM: None known.

Notes

This protocol has been withdrawn as the author team is unable to progress to the final review stage.

Withdrawn from publication for reasons stated in the review

References

Additional references

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