Description of the condition
Hepatocellular carcinoma is the most common type of primary liver cancer (Lau 2000; Di Bisceglie 2010). It is also the fifth most commonly occurring cancer worldwide and the third leading cause of cancer death. In 2008, 1.2% (700,000) of all deaths were due to hepatocellular carcinoma (WHO 2012). Hepatocellular carcinoma incidence varies worldwide. Traditionally, some countries with high endemicity of hepatitis B (eg, China, Southeast Asia, and sub-Saharan Africa) have had higher incidence of hepatocellular carcinoma. People in these countries become infected with hepatitis B virus at an earlier age compared to people living in high-income countries. However, since the early 2000s, high-income countries have also seen an increased incidence of hepatocellular carcinoma. This seems to be related to a rise in other risk factors such as alcoholism, hepatitis C, and type 2 diabetes mellitus (Davila 2004; Hassan 2010; McGlynn 2011). Additional risk factors can include aflatoxin B
The overall prognostic outlook remains poor once hepatocellular carcinoma has been diagnosed. Traditional prognostic variables, such as tumour size, lymph node involvement, and liver functions, have not been useful in predicting outcomes. The median survival of untreated people is about one to nine months from diagnosis, depending on the stage and geographical region (Okuda 1985; Calvet 1990; Kakizaki 1997; Yeung 2005). High-income countries have not had optimistic results either; in the US, one-year survival was less than 50% and five-year survival was 16% in last decade (Altekruse 2009; Siegel 2013). People who undergo resection could have better prognosis, with a median survival of around 40 months and five-year survival of 40% to 60% (Katz 2009; Nathan 2009; Zhou 2012). Although resection is considered a curative treatment for hepatocellular carcinoma, five-year recurrence remains at 70% to 100% (Poon 2000), and it is rare to have a long-term disease-free survival after resection (Yeh 2003). Adjuvant treatments may reduce recurrence of hepatocellular carcinoma and lead to better prognosis (Okada 2001).
Description of the intervention
Transarterial embolisation was first used in Japan to treat hepatocellular carcinoma (Doyon 1974). Hepatocellular carcinoma tumours are supplied by branches of the hepatic artery, while normal hepatic tissue receives the majority (two-thirds) of its blood supply from the portal vein (Breedis 1954; Nakashima 1986). It is this idiosyncrasy in vascularisation that is exploited by transarterial embolisation techniques when branches of the hepatic artery are embolised. Transarterial embolisation is usually performed by catheterising the femoral artery under a local anaesthetic, and a catheter is guided into the hepatic artery under direct fluoroscopic visualisation, followed by injection of iodised oil, gelatin, or polyvinyl alcohol particles (Lin 2003; Pua 2008). As its use has become more widespread, transarterial embolisation was augmented using antineoplastic drugs. This is also known as transarterial chemoembolization (Sakamoto 1998; Lee 2002; Liapi 2011).
How the intervention might work
Embolisation of the hepatic artery may lead to ischaemia of the hepatocellular carcinoma and consequent necrosis. Intra-arterial perfusion of antineoplastic drugs (eg, cisplatin, doxorubicin, adriamycin, mitomycin C) may intensify the antineoplastic effect, with higher local drug concentration and fewer systemic adverse effects. The key to the success of transarterial (chemo)embolization is the exact identification of the arteries supplying the hepatocellular carcinoma and selectively (chemo)embolising them. Important complications of transarterial embolisation/transarterial chemoembolization include vascular perforation, portal vein thrombosis, deterioration of hepatic function, liver abscess and subsequent sepsis, tumour rupture, gastrointestinal bleeding, and postembolization syndrome (Kurokawa 2006).
Transarterial embolisation/transarterial chemoembolization has been used as adjunctive treatment during hepatectomy and as a bridge for liver transplantation, among other indications. It has been used for both resectable and unresectable hepatocellular carcinomas, although evidence for its effectiveness is lacking (Chua 2010; Oliveri 2011). Survival following curative resections is also unsatisfactory. Intrahepatic recurrence following hepatectomy at three years was more than 50% and at five years it was 70% (Otto 1998; Imamura 2003). Most of these recurrences occurred early, within six months (Lu 2008), and are likely to be related to intrahepatic metastases (Poon 2011). The early use of transarterial embolisation/transarterial chemoembolization following hepatectomy may reduce the likelihood of intrahepatic metastases and thereby help reduce recurrence and improve survival.
Why it is important to do this review
Various interventions for hepatocellular carcinoma have been used, either singly or in combination. These have included surgical interventions (eg, tumour resection, cryosurgery, liver transplantation), percutaneous interventions (eg, ethanol, radiofrequency ablation), transarterial interventions (eg, embolisation, chemoembolization), immunotherapy, or hormonal therapy. Curative treatments such as tumour resection and liver transplantation seem ideal. However, only 30% of people are eligible (Rampone 2009). For advanced stages of the tumour, treatments such as tamoxifen, octreotide, and interferon have proved unsuccessful, and more recently, sorafenib has shown promise, but it needs further evaluation (Zhang 2010).
Postoperative transarterial embolisation/transarterial chemoembolization may enhance the curative effects of hepatectomy by erasing the tumour cells that were not removed by surgery, but several studies have reported mixed results (Izumi 1994; Li 1995; Li 2006; Peng 2009; Zhong 2009). Some meta-analyses have reviewed this and suggested that postoperative adjuvant transarterial embolisation/transarterial chemoembolization is a promising method (Mathurin 2003; Marelli 2006; Lau 2009; Zhong 2010). However, there have been concerns about their methodological quality of these studies. It is important to evaluate the available evidence systematically in order to provide objective information to policy-makers and patients who may be able to make better-informed choices of the treatment options available for this condition. We have been unable to identify any systematic reviews on the topic.
To evaluate systematically the available literature of randomised clinical trials regarding the benefits and harms of transarterial (chemo)embolisation as a postoperative adjuvant treatment in people who have undergone hepatectomy for hepatocellular carcinoma.
Criteria for considering studies for this review
Types of studies
We will include all randomised clinical trials that fulfil the inclusion criteria of this review protocol. Non-randomised controlled clinical studies and quasi-randomised controlled clinical studies that otherwise fulfil the inclusion criteria of this review will be considered for the report of data on harms only.
Types of participants
We will include participants who underwent hepatectomy and were diagnosed with hepatocellular carcinoma through pathology methods (eg, histology or cytology). This will be irrespective of tumour type or stage of the disease. We will exclude all participants with distant metastases.
Types of interventions
We will assess transarterial embolisation/transarterial chemoembolization (irrespective of drugs, dosage, duration, interval between each course, instrument, and experience of operators) compared with no intervention, placebo, or sham. Symptomatic treatments and other co-interventions will be allowed if they are comparable in all trial intervention groups.
Types of outcome measures
1. All-cause mortality.
2. Morbidity - transarterial embolisation/transarterial chemoembolisation-related morbidity: liver failure, liver abscess or biloma (infected hepatic fluid collections), acute renal failure or hepatic infarction occurring within six weeks and at a maximal follow-up after the last transarterial embolisation/transarterial chemoembolization (Kim 2010).
3. Clinically serious adverse events: defined as life-threatening or requiring special interventions, according to the International Conference on Harmonisation guidelines (ICH-GCP 2002). Some clinically important adverse events such as vascular perforation, portal vein thrombosis, deterioration of hepatic function, liver abscess and subsequent sepsis, tumour rupture, gastrointestinal bleeding, ascites, and postembolization syndrome, which is defined as abdominal pain, fever, nausea, and vomiting (Chuang 1981), will be specifically analysed if data are available.
4. Quality of life - as measured in individual trials.
1. Tumour recurrence:
1.1 Number of participants with tumour recurrence.
1.2 Time to tumour recurrence.
2. Hospital stay:
2.1 Time to discharge: defined as the hospital stay after transarterial embolisation/transarterial chemoembolization.
2.2 Re-admission to hospital.
Search methods for identification of studies
We will search the Cochrane Hepato-Biliary Group Controlled Trials Register (Gluud 2013), the Cochrane Central Register of Controlled Trials (CENTRAL) in The Cochrane Library, MEDLINE, EMBASE, Science Citation Index Expanded (Royle 2003), Latin American Caribbean Health Sciences Literature (LILACS), CancerLit, Wiley Online Library, POPLINE, Chinese databases (which include Chinese Biomedical Literature Database, China National Knowledge Infrastructure, and the Chongqing VIP Information Co., Ltd., (CQVIP) (formerly known as Database Research Center under Chongqing Branch of Institute of Scientific & Technical Information of China (CB-ISTIC), ie, Chinese journal database research institution), Japan Information Center of Science and Technology File on Science, Technology and Medicine (JICST-E), Australasian Medical Index (AMI), the American Society of Clinical Oncology (ASCO), the National Centre for Complementary and Alternative Medicine (NCCAM), The Allied and Complementary Medicine Database (AMED) and the Campbell Library. We will screen Clinicaltrials.gov (www.clinicaltrials.gov/) and the World Health Organization (WHO) International Clinical Trials Registry Platform (www.who.int/ictrp/en/) for any ongoing trials. We will not apply language or year restrictions. Details of the preliminary search strategies with the expected time spans of the searches are outlined in Appendix 1.
Searching other resources
We will handsearch references of all relevant studies and meta-analyses for any additional trials. We will endeavour to obtain any unpublished studies by contacting the corresponding authors, drug companies, and equipment manufacturers of any relevant studies. We will also contact centres that are involved in this research to determine if there are any unpublished data. We will handsearch reports, posters, and abstracts of relevant conferences.
Data collection and analysis
We will conduct the review according to the recommendations laid out in The Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) and the Cochrane Hepato-Biliary Group module (Gluud 2011).
Selection of studies
Two review authors (QZ and XLB) will work independently and inspect all citations and abstracts (where available) of studies identified by our search in order to identify potentially relevant reports. Another review author (HL) will obtain full-text reports of papers identified by QZ and XLB for a second screen. QZ and XLB will then inspect all these full reports independently and decide about inclusion and exclusion for this review. Any disputes that arise during this process will be arbitrated by HL. If we are unable to reach agreement at this stage, we will contact the authors of these reports for further information to enable us make a decision, and in the meantime, the reports will be placed under the awaiting classification category. If we receive no reply or clarification, then we will ask a colleague to arbitrate.
Data extraction and management
QZ and WC will independently extract data from the included trials. We will translate non-English papers from Chinese prior to data extraction. For trials that have multiple publications, we will identify the one report with the most data and mark it as the 'primary publication'. All studies relating to it will be listed under that one trial. We will extract data from all study reports relating to it and combine them depending on the nature of the reports (Higgins 2011). We will discuss any disagreements with another review author (TM). If necessary, we will contact authors of the identified papers to obtain clarification.
Forms: we will prepare a data extraction form to extract data. The form will include the following information.
- General information: title, authors, contact address, source, published or not, country of publication, year of publication, language of publication, publication type, and sponsors of trial.
- Study eligibility: type of study, participants, interventions, and outcomes.
- Study characteristics: study inclusion/exclusion criteria, randomisation procedure, allocation concealment, blinding, setting, study intervention, study control, and duration of follow-up.
- Participants: inclusion/exclusion criteria, sample size, baseline characteristics (eg, age, sex, ethnicity), information of disease (eg, stage, grade, tumour size), numbers randomised and allocated, and reasons for loss to follow-up/withdrawal.
- Interventions: route, types of drug deliveries, dosage, types of embolisation agents and chemotherapy drugs, duration and frequency of chemotherapy, co-interventions, comparison interventions, and any additional medical therapy.
- Outcomes: hazard ratios (HR), P or Chi
2values, observed number of events, number of total events, survival/mortality, adverse events, mortality, quality of life, duration of hospital stay, and others listed above under outcomes.
QZ and WC will independently extract data and will verify data against the original reports, and we will contact authors for additional data if there are lacking data or there are any discrepancies.
We may come across scale-derived data for outcomes such as quality of life. For outcomes that have been reported using scale-derived data, we will only use them if the scale has been validated (Marshall 2000), and not been modified by individual trialists. Scale-derived data will be our preferred choice as it will be easier to interpret from a clinical point of view. If there are both final and change scores available from the scales used, these will be combined in the analysis as long as we can legitimately do so using appropriate means and standard deviations, and avoiding standardised mean differences (Higgins 2011, Chapter 18.104.22.168).
Assessment of risk of bias in included studies
QZ and WC will independently assess the risk of bias in accordance with The Cochrane Collaboration's tool for assessing risk of bias (Higgins 2011), and the Cochrane Hepato-Biliary Group module (Gluud 2013). We will assess random sequence generation, allocation concealment, blinding, completeness of outcome data, selective reporting, and other biases (Schulz 1995; Moher 1998; Kjaergard 2001; Wood 2008; Lundh 2012; Savović 2012b; Savović 2012a).
Allocation sequence generation
- Low risk of bias: sequence generation was achieved using computer random number generation or a random number table. Drawing lots, tossing a coin, shuffling cards, and throwing dice are adequate if performed by an independent person not otherwise involved in the trial.
- Uncertain risk of bias: the method of sequence generation was not specified.
- High risk of bias: the sequence generation method was not random.
- Low risk of bias: the participant allocations could not have been foreseen in advance of, or during, enrolment. Allocation was controlled by a central and independent randomisation unit. The allocation sequence was unknown to the investigators (eg, if the allocation sequence was hidden in sequentially numbered, opaque, and sealed envelopes).
- Uncertain risk of bias: the method used to conceal the allocation was not described so that intervention allocations may have been foreseen in advance of, or during, enrolment.
- High risk of bias: the allocation sequence was likely to be known to the investigators who assigned the participants.
Blinding of participants, personnel, and outcome assessors
- Low risk of bias: blinding was performed adequately, or the assessment of outcomes was not likely to be influenced by lack of blinding.
- Uncertain risk of bias: there was insufficient information to assess whether blinding was likely to induce bias in the results.
- High risk of bias: no blinding or incomplete blinding, and the assessment of outcomes was likely to be influenced by lack of blinding.
Incomplete outcome data
- Low risk of bias: missing data were unlikely to make treatment effects depart from plausible values. Sufficient methods, such as multiple imputation, have been employed to handle missing data.
- Uncertain risk of bias: there was insufficient information to assess whether missing data in combination with the method used to handle missing data were likely to induce bias in the results.
- High risk of bias: the results were likely to be biased due to missing data.
Selective outcome reporting
- Low risk of bias: all outcomes were predefined and reported, or all clinically relevant and reasonably expected outcomes were reported.
- Uncertain risk of bias: it is unclear whether all predefined and clinically relevant and reasonably expected outcomes were reported.
- High risk of bias: one or more clinically relevant and reasonably expected outcomes were not reported, and data on these outcomes were likely to have been recorded.
For a trial to be assessed as having low risk of bias in the selective outcome reporting domain, the trial should have been registered either on the www.clinicaltrials.gov web site or a similar register, or there should be a protocol (eg, published in a paper or in an online journal). In the case of trials run and published in the years when trial registration was not required, we will carefully scrutinise all publications reporting on the trial to identify the trial objectives and outcomes. If usable data on all outcomes specified in the trial objectives are provided in the publication's results section, then the trial can be considered to have low risk of bias for the selective outcome reporting domain.
- Low risk of bias: the trial appears to be free of industry sponsorship or other types of for-profit support that may manipulate the trial design, conductance, or results of the trial.
- Uncertain risk of bias: the trial may or may not be free of for-profit bias as no information on clinical trial support or sponsorship was provided.
- High risk of bias: the trial was sponsored by the industry or has received another type of for-profit support.
In our review, although the trials we expect to find are perhaps open-labelled trials, we will only categorise these trials as low risk of bias if all the mentioned domains are judged to be of low risk of bias. Otherwise, we will classify trials as being at high risk of bias.
If there are any discrepancies, the review author TM will be the arbitrator. If it is difficult for TM to make a judgement, or if one of the review authors strongly disagrees, or more details are needed, we will contact the authors of the publications for further information.
Measures of treatment effect
We will use Review Manager 5.2 to perform statistical analysis (RevMan 2012), following the principles and recommendations set out in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), and the Cochrane Hepato-Biliary Group module (Gluud 2013).
We will express dichotomous outcomes as risk ratio (RR) with 95% confidence intervals (CI).
We will express continuous outcomes as mean difference (MD). We will calculate standardised mean difference (SMD) only if different validated scales have been used to measure the same outcome.
If count data were used to express some events that can happen to a participant more than once, such as adverse events or hospitalisation, we will use either rate ratio or MD to compare the effects between intervention and control groups, depending on the frequency of the events.
Ordinal outcome data
Where necessary, we will use methods for dichotomous or continuous data to summarise ordinal outcome data, depending on the length of ordinal scales and the analyses reported by the investigators.
Investigators could have reported data on survival, tumour recurrence, and duration of hospital stay as time-to-event data. We will use the method of survival analysis and express the intervention effect as a hazard ratio, and exclude censored participants (ie participants who contribute for some period of time but are without an event).
Unit of analysis issues
Randomised clinical trials with non-standard design, such as cluster trials, cross-over trials, and trials with multiple treatment groups, may present statistical problems. In these situations, studies will be documented and care will be taken to avoid 'unit of analysis' errors when we analyse them (Higgins 2011). We do not anticipate cross-over or cluster randomisation designs, but we do expect multiple intervention groups.
For repeated observations, such as survival at different time points, we will perform separate analyses for the different periods of follow-up, such as short-term (up to one year), medium-term (one to three years), and long-term (beyond five years) follow-up. As for events that may re-occur, we will treat them as count data as mentioned in the Measures of treatment effect section.
Dealing with missing data
We will perform an intention-to-treat (ITT) analysis if possible or available case analysis if ITT analysis is not possible, irrespective of the dropout rates. We will further address the potential impact of missing data on the findings of the review in the Discussion section (Higgins 2011).
Regarding primary outcomes with missing data, we will conduct an ITT analysis according to the scenarios below (Hollis 1999; Gluud 2011). We will indicate in the review where these methods have been used.
- Poor outcome analysis: assuming that dropouts/participants lost from both the experimental and the control arms experienced the outcome, including all randomised participants in the denominator.
- Good outcome analysis: assuming that none of the dropouts/participants lost from the experimental and the control arms experienced the outcome, including all randomised participants in the denominator.
- Extreme case analysis favouring the experimental intervention ('best-worse' case scenario): none of the dropouts/participants lost from the experimental arm, but all of the dropouts/participants lost from the control group experienced the outcome, including all randomised participants in the denominator.
- Extreme case analysis favouring the control ('worst-best' case scenario): all dropouts/participants lost from the experimental arm, but none from the control arm experienced the outcome, including all randomised participants in the denominator.
Available case analysis
If ITT analysis is not possible, we will include data from the available results, and consider the 'best-worst' case and the 'worst-best' case scenario imputations as the span of potential outcomes.
Assessment of heterogeneity
Three review authors (TBL, XLB, and YZ) will independently inspect all included trials to judge the clinical heterogeneity without prior knowledge of comparison data. Clinical diversity may come from type, dose, and duration of antineoplastic drugs used; procedures; co-intervention; stage of disease; and characteristics of participants. If there are clear unforeseen issues or data on outliers that can increase obvious clinical diversity, we will consider these in the analyses and perform separate sensitivity analyses for the primary outcomes. We will resolve any disagreements by an in-depth discussion within our review team.
We will use a Chi
Assessment of reporting biases
Reporting bias arises when the dissemination of research findings is influenced by the nature and direction of results (Higgins 2011). We are aware that funnel plots are useful in investigating bias of any cause. Asymmetric funnel plots are not necessarily caused by reporting bias. Therefore, we will not use funnel plots for outcomes where there are fewer than 10 studies. In other cases, where funnel plots are possible, besides a visual assessment, we will use two tests to assess funnel plots asymmetry (ie rank correlation test (Begg 1994) and regression asymmetry test (Egger 1997)).
We will use Review Manager 5.2 to perform the analyses (RevMan 2012). We will use a random-effects model and a fixed-effect model for each planned meta-analysis. If we find a discrepancy between the two models (ie, one model gives a significant intervention effect while the other shows non-significant intervention effect), we will report both results; otherwise, only the results from the random-effects model will be reported.
Trial sequential analysis
We will apply trial sequential analysis for the reason that cumulative meta-analyses are at risk of producing random errors due to sparse data and repetitive testing of the accumulating data (Brok 2008; Wetterslev 2008; Brok 2009; Thorlund 2009; Wetterslev 2009; Thorlund 2010; Thorlund 2011). To minimise random errors, we will calculate the required information size (ie, the number of participants needed in a meta-analysis to detect or reject a certain intervention effect) (Brok 2008; Wetterslev 2009; Thorlund 2010). The required information size calculation should also account for the heterogeneity or diversity present in the meta-analysis (Brok 2008; Wetterslev 2008; Brok 2009; Thorlund 2009; Wetterslev 2009; Thorlund 2010; Thorlund 2011). In our meta-analysis, the required information size will be based on the event proportion in the control group; assumption of a plausible RR reduction of 20%, or on the RR reduction observed in the included trials with low risk of bias: a risk of type I error of 5%; a risk of type II error of 20%; and the assumed heterogeneity or diversity of the meta-analysis (Brok 2008; Wetterslev 2008; Brok 2009; Thorlund 2009; Wetterslev 2009; Thorlund 2010; Thorlund 2011). The underlying assumption of trial sequential analysis is that testing for significance may be performed each time a new trial is added to the meta-analysis. We will add the trials according to the year of publication, and if more than one trial has been published in a year, trials will be added alphabetically according to the last name of the first author. On the basis of the required information size, trial sequential monitoring boundaries will be constructed (Wetterslev 2008; Thorlund 2009). These boundaries will determine the statistical inference we may draw regarding the cumulative meta-analysis that has not reached the required information size; if the trial sequential monitoring boundary is crossed before the required information size is reached, firm evidence may perhaps be established and further trials may turn out to be superfluous. In contrast, if the boundary is not surpassed, it is most probably necessary to continue doing trials in order to detect or reject a certain intervention effect. We will use the Trial Sequential Analysis (TSA) software application from Copenhagen Trial Unit (CTU 2011; Thorlund 2011).
Subgroup analysis and investigation of heterogeneity
Once all data are extracted and entered, we will perform subgroup analyses and meta-regression analyses to explore the causes of any heterogeneity. Subgroup analyses and meta-regression analyses will be based on a random-effects model due to the high risk of false-positive results when comparing subgroups in a fixed-effect model (Higgins 2004). We will perform subgroup analyses for:
- trials with low risk of bias compared to trials with high risk of bias.
- type of intervention: transarterial embolisation compared to transarterial chemoembolization;
- co-interventions: trials with co-intervention compared to trials without co-intervention;
- type of antineoplastic drugs: individual antineoplastic drug used for transarterial chemoembolization.
Should heterogeneity remain unexplained despite our efforts, we may present the final data without a meta-analysis.
We will perform sensitivity analyses to evaluate the robustness of results of primary outcomes in trials with missing data or possible sources of clinical diversity.
- Missing data: we will use sensitivity analyses to judge the assumptions of the ITT method used (see Dealing with missing data) to determine if results of primary outcomes are stable.
- Possible sources of increased clinical diversity: for example, participants with intrahepatic recurrence who underwent a second surgery may have higher number of metastasis and shorter survival time.
See 'Dealing with missing data' for the other planned sensitivity analyses.
'Summary of findings' tables
We will use the GRADE approach (http://ims.cochrane.org/revman/other-resources/gradepro) to assess the quality of a body of evidence (Higgins 2011) and present the results of the outcomes in a 'Summary of findings' tables.
We would like to thank Dimitrinka Nikolova, the Managing Editor, and Sarah Louise Klingenberg, Trials Search Co-ordinator, for their advice during the preparation of this review protocol.
We would also like to thank the National Natural Science Funds for Distinguished Young Scholar (No. 30925033), the National Natural Science Fund of China (No. 30801101), the Natural Science Fund of Zhejiang Province, China (No. Z2080283), and the Science and Technology Planning Project of Zhejiang Province, China (No. 2007C33075) for financial support of our work.
Peer reviewers: Tim Meyer, UK; Frank T. Kolligs, Germany.
Contact editors: Vanja Giljaca, Croatia; Kurinchi Gurusamy, UK.
Appendix 1. Search strategies
Contributions of authors
Qi Zhang prepared the draft protocol. XLB, WC, TM, HL, YZ, XJH, and TBL commented on and approved the final protocol for publication.
Declarations of interest
No conflicts of interest to declare.
Sources of support
- The Second Affiliated Hospital, Zhejiang University School of Medicine, China.Salary support.
- Department of Hepatobiliary and Pancreatic Surgery, the Second Affiliated Hospital, Zhejiang University School of Medicine, China.Hardware facility and office supplies support.
- National Natural Science Funds for Distinguished Young Scholar (No. 30925033), China.Financial support.
- National Natural Science Fund of China (No. 30801101), China.Financial support.
- Natural Science Fund of Zhejiang Province, China (No. Z2080283), China.Financial support.
- Science and Technology Planning Project of Zhejiang Province, China (No. 2007C33075), China.Financial support.