Study Design

Two systematic reviews(SR), published in 2015¹⁹ and 2016²⁰ were identified. Both SRs sought randomized controlled trials (RCT) published until December, 2014,¹⁹ or until May, 2016.²⁰ Each SR included 11 RCTs, and both used the Cochrane Risk of Bias tool to critically appraise included studies.^19,20 There was overlap between nine of the included the studies in the two SRs, and this is detailed in Appendix 5.

Three randomized controlled trials^21–23 (RCT) and four non-randomized, observational studies^24–27 were also identified by this review. One RCT specified the duration of follow-up per outcome i.e., for women with live birth, women were followed throughout pregnancy and children were followed to two years; for patients with spontaneous abortion, follow-up was until loss of pregnancy and; for patients who did not conceive, follow-up ended at 12 months.²¹ The remaining studies included in this review either did not specify follow-up duration^{22,23,25–27} or did not report follow-up clearly.²⁴ Of the non-randomized studies, two were prospective,^24,26 and two were retrospective.^25,27

Country of Origin

One SR was based in China,²⁰ and the another SR was conducted by authors from Denmark.¹⁹ The RCTs were conducted in China,²¹ Denmark,²² and Iran.²³ Two of the four non-randomized, observational studies were conducted in Spain,^25,26 and the other two were conducted in Iran²⁴ and Korea.²⁷

Patient Population

One SR reported data from studies evaluating 582 pregnant patients with a history of ≥2 consecutive, recurrent, spontaneous abortions (RSA).²⁰ The other SR reported on 531 people with a history of 3 or more consecutive, spontaneous abortions.

The three RCTs limited their recruitment to people with a history of 3 or more consecutive, spontaneous abortions. One RCT randomly allocated 192 participants to either the intervention or comparison arms of the study.²¹ Participants were recruited from a specialty miscarriage center in Korea and had a mean age of 31.2 years (SD ±3.7) in the intervention group and 31.6 (SD ±4.2) years in the comparison group (P = 0.81).²¹ Another RCT recruited and randomized 82 pregnant patients with secondary RSA from a recurrent miscarriage clinic in Denmark, with 42 patients allocated to the intervention arm (mean age 34.5 years, 95% CI 26.2-40.9) and 40 allocated to the comparison arm (mean age 34.2 years, 95% CI 26.1-41.0).²² The third RCT included in this review randomized 60 participants from a hospital-based Obstetrics and Gynecology department to either the intervention or comparison arms of the trial. The mean age of patients in the intervention arm of the study was 29.7 years (SD ±3.1), and in the comparison arm was 31.2 years (SD ±2.1).²³

Both of the prospective, non-randomized studies limited recruitment to participants with a history of 3 or more consecutive, spontaneous abortions.^24,26 One study was a controlled clinical trial of 94 participants recruited from a hospital-based infertility center in Iran with a mean age of 33.8 years (SD ±3.6) in the intervention arm and 34.1 years (±SD 3.4) in the comparison group. The other prospective, non-randomized study used a case-control design investigating 64 participants recruited from a hospital-based immunology clinic in Spain with either RSA (n=24) or recurrent implantation failure (n=40); the latter of which were not eligible for inclusion within the current review. Among the nested cohort of 24 eligible participants with RSA, those in the intervention group had a mean age of 35.7 years (SD ±4.4) and those in the comparison group had a mean age of 37 years (SD±5.1).²⁶

Patients evaluated within the two retrospective, non-randomized studies had a history of either 2 or more ²⁷ or 3 or more consecutive, RSA.²⁵ The former reviewed medical records and stratified participants based on the findings of an etiological assessment of their history of RSA from a hospital-based Obstetrics and Gynecology department in Korea.²⁷ The latter study examined 428 participants with recurrent reproductive failure – including 217 with RSA²⁵ and a mean age of 36.48 (SD ±3.63, range 27 to 43) who were eligible for analysis in the current review.

Interventions and Comparators

The interventions of interest in one SR were IVIG before or during early pregnancy compared with placebo;²⁰ and in the other SR were IVIG compared with placebo, no treatment, or standard care.¹⁹ Duration, dosing, and frequencies varied across included studies.^19,20

The three RCTs all examined various regimens of IVIG compared with various active comparators.^21–23 The Chinese trial administered pre-pregnancy treatment on a three-month alternating schedule (i.e., three months on treatment; three months off treatment) until either pregnancy was achieved or 24 months of alternating treatment was complete. Patients in the intervention arm received IVIG (25 grams (g)) on days eight, nine, or 10 of the menstrual cycle and every month until pregnancy was achieved, followed by once per week until 12 weeks gestation.²¹ The comparison group was treated with intravenous (IV) intralipid (20%; 250 millilitres (mL)) on day three of the patients’ menstrual cycles and every two weeks thereafter until pregnancy was achieved; at which time, the frequency of IV intralipid was increased to once per week until 12 weeks gestation.²¹ In the Danish trial, two different regimens of IVIG were administered across the almost-six years of the study, due to the drug brand becoming unavailable in 2011.²² From August 2008 to May, 2011, the intervention arm received eight infusions of IVIG (120 mg/ml) until between 14 and 15 weeks gestation with dose dependent on body weight ²² The comparison group received a placebo intervention comprised of eight infusions of albumin (5%) with dose dependent on body weight.²² As of May, 2011, patients in the intervention arm continued to receive eight infusions of IVIG (100 milligrams (mg)/mL) until between 14 and 15 weeks gestation, and the comparison group remained on a similar regimen of eight infusions to between 14 and 15 weeks gestation, with doses of both medications dependent on body weight²² (details provided in Appendix 2). The Iranian trial administered daily subcutaneous enoxaparin (40 mg) until 24 weeks gestation and daily aspirin (80mg) until 37 weeks gestation to both the intervention and comparison groups.²³ In addition, the intervention group received IVIG (200 milligrams (mg)/kilogram (kg) body weight) each month until 24 weeks gestation.²³

All of the non-randomized studies investigated IVIG (400 mg/kg body weight) using various regimens and comparators.^24–27 The prospective, controlled clinical trial administered IVIG to patients in the intervention arm from confirmation of pregnancy to 32 weeks gestation, whereas patients in the comparison arm received standard care.²⁴ Patients in the intervention arm of the prospective Spanish study received IVIG every three to four weeks until 13 weeks gestation, followed by 200 mg/kg monthly until 35 weeks gestation (IVF patients received an additional dose at both 24 hours and 15 days following confirmed pregnancy).²⁶ There was no information reported concerning whether patients in the comparison group of this study received any treatment or not.²⁶ In the Korean study, patients who had thrombophilia were administered daily, low-dose aspirin (100 mg) and subcutaneous, low-molecular-weight heparin (2,500 IU).²⁷ Patients with cellular immune abnormality received IVIG once every three weeks from between four and six weeks to 30 weeks gestation. Patients with neither thrombophilia nor cellular immune abnormality received standard care.²⁷ Finally, the retrospective Spanish study reported administration of IVIG once every three weeks in the first trimester of pregnancy, followed by 200 mg/kg every four weeks until between 35 and 36 weeks gestation, plus acetyl salicylic acid (100 mg; frequency and duration not reported), with additional doses (400 mg/kg) for IVF patients at 24 hours and 15 days following confirmed pregnancy.²⁵ Patients in the comparison group received acetyl salicylic acid (100 mg) with or without an unspecified dose of low molecular weight heparin for patients with prothrombotic and/or cardiovascular risk factors.²⁵

Outcomes

Live births and/or live birth rates were reported in all of the included studies.^19–27 In one SR, live birth rate was defined as live births per pregnancies achieved and was analyzed using random effects models, and both cumulative meta-analyses and trial sequential analyses.²⁰ Subgroup analyses included a comparison of patients with either primary (no history of live birth) or secondary (history of at least one live birth) RSA, and administration of IVIG prior to conception as opposed to following implantation of the embryo.²⁰ Another SR stated its primary outcome of interest as no live birth, with secondary outcomes of interest including adverse events and quality of life analyzed using both meta-analyses and trial sequential analyses.¹⁹ Subgroup analyses in this SR focused on patients with primary versus secondary RSA and low- versus high-dose IVIG.¹⁹

The three RCTs all investigated live births, adverse events or side effects, and neonatal outcomes.^21–23 Successful pregnancies were the primary outcome in one RCT and defined as those that reached 12 weeks gestation.²¹ This study also measured live births, side effects, and neonatal growth parameters (of which neither of the two latter outcomes/measures were pre-specified in detail), as well as cellular outcomes (i.e., nonclinical) that were not eligible for inclusion in this review ²¹ Another RCT calculated and compared live birth rate per treatment group as its primary outcome of interest, defined as the number of participants giving birth to a neonate surviving to at least 28 days of life over all those randomized.²² This study also recorded neonatal parameters, including birth weight, gestational length, Apgar scores of less than 10 and days in the NICU, as well as adverse events (not further detailed a priori).²² The remaining RCT included in this review investigated live birth (not further defined) as its primary outcome, as well as obstetric, perinatal, and neonatal outcomes, including preeclampsia, pre-term labour, gestational diabetes, low birth weight, congenital defects, and gestational age and side effects (including urticarial; bleeding; pain; irritation; hematoma at the injection site, and; ecchymosis).

The direction of effect to indicate a clinical improvement was self-evident for the main outcomes of interest i.e., more live births and fewer adverse events/side effects were indicators of clinical benefit. The minimally important difference to detect a clinical effect was addressed by way of sample size calculations in three of the studies included in this review i.e., two RCTs^22,23 and one non-randomized, observational study.²⁴ One RCT specified that, to detect an assumed 70% versus 33% live birth rate in the intervention versus control groups, respectively, a required sample size of 41 patients per treatment group was needed.²² Another RCT reported that 30 patients would be needed per group to generate 80% power to detect a difference between groups.²³ Finally, one nonrandomized, controlled clinical trial reported that, to identify an assumed difference of 75% versus 40% live birth rate between intervention and control groups, respectively, 44 study participants per group was necessary.²⁴

Additional details regarding the characteristics of included publications are provided in Appendix 2.

Systematic Reviews

Both systematic reviews included in this review^19,20 demonstrated strengths and limitations. In terms of strengths, both SRs reported the conduct of study selection and data abstraction by two independent reviewers, and both described comprehensive literature searches with a detailed list of included studies. Both conducted critical appraisal of included studies and performed appropriate meta-analyses. However, whereas one SR made explicit mention of a protocol,¹⁹ the other did not.²⁰ Protocols are an important feature of systematic reviews as they allow for the assessment of an a priori method and thus the extent to which risk of bias that may be present. Similarly, while one SR formally assessed publication bias,²⁰ the other did not describe a formal assessment.¹⁹ Publication bias in SR is an important factor in understanding the extent to which findings from included, published studies may over represent a positive effect. Again, while one SR explicitly addressed publication status,¹⁹ the other did not,²⁰ leaving uncertainty with regard to the latter SR as to whether its included studies are representative of the entire body of both published and unpublished evidence. Finally, while neither of the SRs reported sources of funding supporting the included studies, one reported the source of funding for the SR itself,¹⁹ whereas the other did not.²⁰ Transparency with regard to funding support is a critical feature of SR, allowing the reader to assess the credibility and any potential conflict of interest for both the studies included in the SR, as well as the work completed on the SR itself.

Randomized Controlled Trials

Clarity of reporting is critical to a transparent assessment of the strengths and limitations of studies included in any review. Study reporting was clear for some criteria across the three RCTs included in this review, with main outcomes, patient characteristics, interventions, random variability and adverse events reported.^21–23 Nonetheless, other criteria were not consistently reported across RCTs i.e., study aim and objectives were reported clearly in two^21,22 but not in one of the RCTs;²³ main findings and loss to follow-up were clearly reported in two ^22,23 but not in one of the RCTs;²¹ probability values were clearly reported in one RCT,²² partially reported in another ²¹ and not clearly reported in the third RCT.²³ Finally, as it concerned reporting, all three RCTs failed to provide an explicit list of principal confounders.^21–23 Because some information was lacking from the reports of the studies included in this review, they could not be assessed in their entirety.

It was not possible to assess any of the items addressing external validity for the included RCTs, as details about the representativeness of subjects asked to participate; patients who consented to participate, and; the interventions administered, were either not reported or not reported in enough detail to assess.^21–23 Because external validity could not be ascertained for the RCTs, it remains unclear whether their findings can appropriately be applied to other, similar patients.

An understanding of internal validity in general, and risk of bias in particular, is critical to informing the interpretation of a study. In this review, risk of bias was assessed as variable across the three RCTs i.e., while one of the trials demonstrated no evidence of a threat to internal validity by way of bias in its report of findings,²² both of the other RCTs were assessed as demonstrating some risk of bias.^21,23 In terms of strengths, both RCTs demonstrated no evidence of unplanned analyses, used ostensibly appropriate statistical tests, and presented detailed descriptions of appropriate outcome measures.^21,23 However, whereas one clearly reported consistent duration of patient follow-up²³, the other did not.²¹ Further, both remaining RCTs did not describe any method to ensure patients or outcome assessors were blinded to the interventions and patient compliance with the interventions was not described.^21,23 Thus, the effects reported in the two RCTs with a higher risk of bias should be interpreted with caution as this may have had an impact on the effects reported.

Risk of confounding is an important consideration in weighing whether the effect demonstrated in a study can be isolated to the intervention and comparator of interest as opposed to other, extraneous factors or characteristics. The risk of any confounding was assessed as being variably present across the RCTs included in this review.^21–23 While all three trials allocated patients to treatment using randomization, ^21–23 only one described randomization concealment.²² Likewise, while study subjects were apparently recruited from the same population over the same time period in all three studies, adjustment for known confounders was not explicitly addressed by any of the included RCTs.^21–23 Lastly, loss to follow-up was clearly accounted for in two of the trials,^22,23 while not clearly accounted for in one RCT.²¹ While all three of the trials were randomized, the limitations of each must be considered when weighing the internal validity of their findings.

Finally, power calculations are critical as part of considering adequacy of the sample size used in a study — which is a fundamental consideration in weighing the importance of its findings and conclusions, as it serves as an indicator of the probability of avoiding a Type II error (i.e., finding an apparent effect among the sampled patients in a study where no effect actually exists). While a power calculation was described in two of the RCTs,^22,23 study power was not addressed in one of the trials,²¹ leaving the reader of the latter study less certain as to the potential for error in its reported findings.

Non-Randomized Studies

The study aims, objectives, and patient characteristics were clearly reported in all four nonrandomized studies, whereas a list of principal confounders and adverse events were not clearly reported in any of these four studies.^24–27 Other reporting characteristics were reported variably with some of the four non-randomized studies clearly reporting main outcomes, interventions, main findings, random variability, loss to follow-up and probability values, and some either not reporting these criteria at all, or only partially.^24–27 In particular, one study reported live birth in 121 of 217 enrolled patients with no clear explanation as to why this outcome was not reported in the full study population.²⁵ Because at least some information was lacking from all of the reports of the non-randomized studies included in this review, the studies could not be assessed with regard to all critical appraisal criteria.

As with the RCTs in this review, all four non-randomized studies provided insufficient information as to the representativeness of their study participants,^24–27 preventing an assessment of external validity. This is a particularly important limitation, as it leaves the reader unclear as to whether the reported findings can appropriately be applied to other, similar patients or not.

An assessment of bias in the four non-randomized studies indicated that all of the studies appeared to have implemented a consistent follow-up duration for study groups, ostensibly appropriate statistical tests, and outcome measures that were clearly described.^24–27 Conversely, all four non-randomized studies reported no information regarding whether patients and outcome assessors were blind to the treatment allocation, as well as whether patients were compliant with the interventions to which they were allocated. Additional measures of internal validity specific to bias were reported variably across the four nonrandomized studies and are detailed in Appendix 3.

Internal validity was also considered in terms of confounding, with all four non-randomized studies included in this review demonstrating some limitations in their address of confounding.^24–27 Perhaps most importantly, none of the non-randomized studies randomized patients to treatment, nor did they clearly report adjustment for potentially confounding variables,^24–27 introducing a risk when considering whether the demonstrated effect can be attributed to the interventions of interest as opposed to other, extraneous factors or characteristics. Further, while two of the non-randomized studies in this review did report that patients from both study groups were recruited from the same centre within the same timeframe,^24,27 two did not.^25,26 Lastly, in three of the non-randomized studies, patients were explicitly allocated to treatment based on clinical or socioeconomic characteristics,^25–27 and in the controlled clinical trial, patient allocation to the control group was described as voluntary.²⁴ These methods for allocating study participants to treatment increase the risk of confounding and reduce certainty as to whether any effect demonstrated by the study was due to the interventions under study as opposed to extant differences between the patient groups being compared.

Finally, sample size and study power were explicitly reported by one non-randomized study in this review,²⁴ but not addressed in the other three.^25–27

Additional details regarding the strengths and limitations of included studies are provided in Appendix 3.

Clinical Effectiveness – Benefit

Clinical Effectiveness – Harm