Criteria for considering studies for this review
Types of studies
Randomised and quasi-randomised controlled trials, as well as cluster-randomised trials, comparing Chinese herbal medicines (alone or combined with other intervention or other pharmaceuticals) with placebo, no treatment, other intervention (including bed rest and psychological supports) or other pharmaceuticals as treatments for recurrent miscarriage. Trials, with or without full text, will be included. No language restrictions will be applied.
Types of participants
All pregnant women diagnosed with unexplained recurrent miscarriage, regardless of maternal age, gestational age and parity, will be studied. In this review, the criteria for recurrent miscarriage will be considered as two or more consecutive spontaneous miscarriages before the 20th week of gestation. No treatment will be given before interventions. In this review, only recurrent miscarriage with unknown underlined causes will be studied. Trials involving women with recurrent miscarriage with identified causes will be excluded. Any studies in which prior miscarriages at ≧ 14 weeks are included and which cannot be separated from first trimester miscarriages will be excluded, as only a minority of embryonic or fetal losses are after 14 weeks.
Types of interventions
All types of Chinese herbal medicines either standalone or in combination with other treatment for recurrent miscarriage, regardless of the dose, dosing or duration of administration, compared with other treatments will be compared. The following comparisons will be studied.
Chinese herbal medicines versus placebo.
Chinese herbal medicines versus no treatment.
Chinese herbal medicines versus other intervention (including bed rest and psychological supports).
Chinese herbal medicines alone versus other pharmaceuticals (mainly Western medicines).
Combined Chinese herbal medicines and other pharmaceuticals versus other pharmaceuticals (mainly Western medicines).
Types of outcome measures
(1) Effectiveness of intervention:
live birth rate.
Pregnancy rate will be defined as successful rate of continuation of pregnancy after 20 weeks of gestation after the treatment. It will be presented as the number of pregnancies alive after 20 weeks of gestation over the total number of participants as a percentage.
Live birth rate will be defined as successful rate of pregnancy with live birth after 28 weeks of gestation. It will be presented as the number of live birth after 28 weeks of gestation over the total number of participants as a percentage.
(2) Safety of intervention:
Adverse effect and toxicity refer to harmful and undesired side-effects and/or toxic effects resulting from the treatment. Specific outcomes of maternal adverse effect and toxicity may include maternal death and all reported obstetric and other complications. The rate will be presented as the number of maternal adverse or toxic events over the total number of participants as a percentage.
Specific outcomes of perinatal adverse effect and toxicity may include perinatal death and all reported complications, premature infant and congenital malformations. The rate will be presented as the number of perinatal adverse or toxic events over the total number of newborns as a percentage.
(3) Obstetric complications (haemorrhage, hypertension, etc).
(4) Other complications (e.g. dry mouth, gastrointestinal discomfort, etc).
(5) Fetal death within 14 weeks.
(6) Fetal death after 14 weeks.
(7) Premature infant (< 37 weeks).
(8) Perinatal complications (small-for-gestational age: birthweight < 10th percentile for gestational age, intrauterine growth restriction, physiopathological jaundice, etc).
(9) Congenital malformations (e.g. limb anomaly such as polydactyly (congenital abnormality of having an extra finger), heart anomaly such as patent ductus arteriosus, nervous system anomaly for example, spina bifida, etc).
Search methods for identification of studies
We will search the Cochrane Pregnancy and Childbirth Group’s Trials Register by contacting the Trials Search Co-ordinator.
The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co-ordinator and contains trials identified from:
monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
weekly searches of MEDLINE;
weekly searches of EMBASE;
handsearches of 30 journals and the proceedings of major conferences;
weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.
Details of the search strategies for CENTRAL, MEDLINE and EMBASE, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service can be found in the ‘Specialized Register’ section within the editorial information about the Cochrane Pregnancy and Childbirth Group.
Trials identified through the searching activities described above are each assigned to a review topic (or topics). The Trials Search Co-ordinator searches the register for each review using the topic list rather than keywords.
In addition, we will search the following databases: EMBASE (1980 to current) ; Cumulative Index to Nursing and Allied Health Literature (CINAHL) (1982 to current) ; Chinese Biomedical Database (CBM) (1978 to current); China Journal Net (CJN) (1915 to current); China Journals Full-text Database (1915 to current); and WanFang Database (Chinese Ministry of Science & Technology) (1980 to current). See Appendix 2; Appendix 3 and Appendix 4 for search strategies.
Searching other resources
(1) References from published studies
We will search the reference lists of relevant trials and reviews identified. We will also screen bibliographies of all located articles for any unidentified articles.
(2) Unpublished literature
If necessary, we will contact the authors for more details about the published trials/ongoing trials and the pharmaceutical companies for more information of medicines/relevant products.
(3) Personal communications
We will contact organisations, individual experts working in the field, and medicinal herbs manufacturers in order to obtain additional references.
We will not apply any language restrictions.
Data collection and analysis
Selection of studies
Two review authors will independently assess for inclusion all the potential studies. We will resolve any disagreement through discussion or, if required, we will consult a third review author.
Data extraction and management
We will design a form to extract data. For eligible studies, two review authors will independently extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult a third review author. We will enter data into Review Manager software (RevMan 2011) and check for accuracy.
When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.
Assessment of risk of bias in included studies
Two review authors will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreement by discussion or by involving a third assessor.
(1) Random sequence generation (checking for possible selection bias)
We will describe for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.
We will assess the method as:
low risk of bias (any truly random process, e.g. random number table; computer random number generator);
high risk of bias (any non-random process, e.g. odd or even date of birth; hospital or clinic record number);
unclear risk of bias.
(2) Allocation concealment (checking for possible selection bias)
We will describe for each included study the method used to conceal allocation to interventions prior to assignment and will assess whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We will assess the methods as:
low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
high risk of bias (open random allocation; unsealed or non-opaque envelopes; alternation; date of birth);
unclear risk of bias.
(3.1) Blinding of participants and personnel (checking for possible performance bias)
We will describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will consider that studies are at low risk of bias if they were blinded, or if we judge that the lack of blinding would be unlikely to affect results. We will assess blinding separately for different outcomes or classes of outcomes.
We will assess the methods as:
low, high or unclear risk of bias for participants;
low, high or unclear risk of bias for personnel.
(3.2) Blinding of outcome assessment (checking for possible detection bias)
We will describe for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We will assess blinding separately for different outcomes or classes of outcomes.
We will assess methods used to blind outcomes assessment as:
(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)
We will describe for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We will state whether attrition and exclusions were reported and the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information is reported, or can be supplied by the trial authors, we will re-include missing data in the analyses which we undertake.
We will assess methods as:
low risk of bias (e.g. no missing outcome data or less than 20% missing; missing outcome data balanced across groups);
high risk of bias (e.g. number or reasons for missing data imbalanced across groups; 'as treated' analysis done with substantial departure of intervention received from that assigned at randomisation);
unclear risk of bias.
(5) Selective reporting (checking for reporting bias)
We will describe for each included study how we investigated the possibility of selective outcome reporting bias and what we found.
We will assess the methods as:
low risk of bias (where it is clear that all of the study's pre-specified outcomes and all expected outcomes of interest to the review have been reported);
high risk of bias (where not all the study's pre-specified outcomes have been reported; one or more reported primary outcomes were not pre-specified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);
unclear risk of bias.
(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)
We will describe for each included study any important concerns we have about other possible sources of bias.
We will assess whether each study was free of other problems that could put it at risk of bias:
(7) Overall risk of bias
We will make explicit judgements about whether studies are at high risk of bias, according to the criteria given in the Cochrane Handbook (Higgins 2011). With reference to (1) to (6) above, we will assess the likely magnitude and direction of the bias and whether we consider it is likely to impact on the findings. We will explore the impact of the level of bias through undertaking sensitivity analyses - see Sensitivity analysis.
Measures of treatment effect
For dichotomous data, we will present results as summary risk ratio with 95% confidence intervals.
For continuous data, we will use the mean difference if outcomes are measured in the same way between trials. We will use the standardised mean difference to combine trials that measure the same outcome, but use different methods.
Unit of analysis issues
We will include cluster-randomised trials in the analyses along with individually-randomised trials. We will adjust their sample sizes using the methods described in the Cochrane Handbook (Higgins 2011) using an estimate of the intracluster correlation co-efficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population. If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster-randomised trials and individually-randomised trials, we plan to synthesise the relevant information. We will consider it reasonable to combine the results from both if there is little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomisation unit is considered to be unlikely.
We will also acknowledge heterogeneity in the randomisation unit and perform a subgroup analysis to investigate the effects of the randomisation unit.
Studies with more than two treatment groups
If we identify any multi-arm trials, we will include these if any pair-wise comparisons of the intervention groups are relevant to the review and meet our inclusion criteria. We will report all the intervention groups involved in the study in the 'Characteristics of included studies', but we will include only those intervention groups relevant to the review in the analysis. We will address pair-wise comparisons in multi-trials in relevant meta-analyses if they are eligible for the analysis, and we will ensure that data from any individual are included only once when pooling data. If there are multiple intervention groups in a particular meta-analysis, we will combine all relevant experimental intervention groups of the study into a single intervention group and combine all relevant control intervention groups into a single control group (Higgins 2011).
Dealing with missing data
For included studies, we will note levels of attrition. We will explore the impact of including studies with high levels of missing data in the overall assessment of treatment effect by using sensitivity analysis.
For all outcomes, we will carry out analyses, as far as possible, on an intention-to-treat basis, i.e. we will attempt to include all participants randomised to each group in the analyses, and all participants will be analysed in the group to which they were allocated, regardless of whether or not they received the allocated intervention. The denominator for each outcome in each trial will be the number randomised minus any participants whose outcomes are known to be missing.
Assessment of heterogeneity
We will assess statistical heterogeneity in each meta-analysis using the T2, I2 and Chi2 statistics. We will regard heterogeneity as substantial if the T2 is greater than zero and either an I2 is greater than 30% or there is a low P value (less than 0.10) in the Chi2 test for heterogeneity.
Assessment of reporting biases
If there are 10 or more studies in the meta-analysis, we will investigate reporting biases (such as publication bias) using funnel plots. We will assess funnel plot asymmetry visually, and use formal tests for funnel plot asymmetry. For continuous outcomes we will use the test proposed by Egger 1997, and for dichotomous outcomes we will use the test proposed by Harbord 2006. If asymmetry is detected in any of these tests or is suggested by a visual assessment, we will perform exploratory analyses to investigate it.
We will carry out statistical analysis using the Review Manager software (RevMan 2011). We will use fixed-effect meta-analysis for combining data where it is reasonable to assume that studies are estimating the same underlying treatment effect: i.e. where trials are examining the same intervention, and the trials' populations and methods are judged sufficiently similar. If there is clinical heterogeneity sufficient to expect that the underlying treatment effects differ between trials, or if substantial statistical heterogeneity is detected, we will use random-effects meta-analysis to produce an overall summary, if an average treatment effect across trials is considered clinically meaningful. The random-effects summary will be treated as the average range of possible treatment effects and we will discuss the clinical implications of treatment effects differing between trials. If the average treatment effect is not clinically meaningful, we will not combine trials.
If we use random-effects analyses, the results will be presented as the average treatment effect with its 95% confidence interval, and the estimates of T2 and I2.
Subgroup analysis and investigation of heterogeneity
If we identify substantial heterogeneity, we will investigate it using subgroup analyses and sensitivity analyses. We will consider whether an overall summary is meaningful, and if it is, use random-effects analysis to produce it.
We plan to carry out the following subgroup analyses:
maternal age: below 35 versus 35 and above;
gestational age at intervention with Chinese herbal medicines started: < 14 weeks versus ≧ 14 weeks;
numbers of prior recurrent miscarriage: two consecutive miscarriages versus more than two consecutive miscarriages;
type of herbal medicines: standard herbal medicines versus non-standard herbal medicines, according to the formulary stated in the Chinese Pharmacopeia;
timing of intervention: before pregnancy versus after pregnancy;
duration of intervention: short-term treatment (one course only) versus long-term treatment (more than one course);
study design: quasi-randomised clinical trials versus randomised clinical trials;
main types of recurrent miscarriage in Chinese Medicine: "Qi" deficiency in Kidney versus combined "Qi" and "Blood" deficiency.
We will use the following outcomes in subgroup analysis:
We will assess subgroup differences by interaction tests available within RevMan (RevMan 2011). We will report the results of subgroup analyses quoting the X2 statistic and P value, and the interaction test I2 value.
We will carry out sensitivity analysis to explore the effect of trial quality on important outcomes in the review. Where there is a high risk of bias in the allocation of participants to groups associated with a particular study or high levels of missing data, we will explore this by sensitivity analysis (Higgins 2011).
We will use the following outcomes in sensitivity analysis:
effectiveness of intervention: pregnancy rate and live birth rate;
pregnancy loss (before and after 14 weeks);
preterm delivery (less than 37 weeks);
obstetric complications (haemorrhage, hypertension, intrauterine growth retardation);