Strategies of testing for syphilis during pregnancy

  • Protocol
  • Intervention

Authors


Abstract

This is the protocol for a review and there is no abstract. The objectives are as follows:

To assess the effectiveness of maternal syphilis screening strategies.

Background

Syphilis is a potentially fatal, sexually transmitted disease (STD) that can be transmitted to the fetus of a pregnant woman infected with syphilis. Though preventable, globally, each year about two million pregnant women become infected with syphilis, the majority of whom live in developing countries (WHO 2011). The yearly toll of adverse birth outcomes associated with untreated maternal syphilis is 730,000 to 1500,000, of which nearly 650,000 deaths occur in fetuses and newborns (Schmid 2007; WHO 2010). Maternal syphilis is less of a concern in developed countries than in developing countries. For example, in congenital syphilis (mother-to-child transmission), the seroprevalence of women with syphilis attending antenatal care is estimated to be highest in Latin America (3.90%) and Africa (1.98%) (Schmid 2007). In Africa alone, syphilis causes nearly 400,000 stillbirths and newborn deaths in a single year (Anonymous 2012). Furthermore, concern is deepening in countries such as China where an increase in the disease incidence has already been observed (Cheng 2007; Tucker 2010). In China in 2008, among 9480 total cases, on average, more than one baby per hour was born with congenital syphilis; the observed amplification rate was by a factor of 12 during the five preceding years (Tucker 2010). Moreover, people with the human immunodeficiency virus infection/acquired immunodeficiency syndrome  (HIV/AIDs) usually become infected with syphilis and vice versa (Walker 2001). As a result, the rise in congenital syphilis in many countries in Sub-Saharan Africa has been aggravated by HIV/AIDs as this region is highly burdened by HIV/AIDs infection (WHO 2010).

The World Health Organization (WHO) has estimated that about 50% of pregnant women with untreated syphilis will transmit the infection to the fetus causing severe birth outcomes such as spontaneous abortion, prematurity, stillbirth, low birthweight, neonatal death, or serious sequelae in liveborn infected children (WHO 2011). However, these adverse outcomes are preventable, and existing health programs such as incorporated sexual and reproductive health programs, antenatal syphilis screening, and timely treatment have been suggested as a means to curtail syphilis-attributable perinatal deaths and stillbirth incidence by about 50% (Bique 2000; Hawkes 2011; Myer 2003; Wilkinson 1998). Hence, every pregnant woman has been urged to undergo routine antenatal check-up (UNICEF 2009; WHO 2007). Yet, for decades, in spite of the existence of an antenatal screening policy in the majority of the countries, policy implementation is typically lacking (Gloyd 2001; Hossain 2007).

Additionally, the control and elimination of syphilis is hindered by the fact that the majority of infected women are not tested; nearly every one of those who is tested either does not undergo prompt treatment or is missed entirely (WHO 2011). Despite the availability of various improved diagnostic tools and cost-effective prevention therapy (Peeling 2004; WHO 2010), the prevention and elimination of syphilis is predominantly disrupted by the complexity of the natural disease history, coupled with the absence of precise clinical presentation in infected patients (Peeling 2004). It has also been suggested that the absence of antenatal care, and poor quality services are likely to be important factors in raising the number of mothers giving birth to newborns with congenital syphilis (Walker 2002; Wilkinson 1998).

Scientific efforts for the prevention and elimination of congenital syphilis have been accelerated by the development of reliable and improved diagnostic tools such as on-site syphilis testing, providing rapid results and immediate therapy for sero-positive women in primary care settings. In addition to laboratory testing, on-site testing might be a useful strategy to curb congenital syphilis and its associated adverse outcomes by reducing treatment delays and increasing the numbers of sero-positive women treated (Delport 1998; Fann 1996; Jenniskens 1995). Although the effects of on-site testing in observational studies (Bique 2000; Temmerman 2000) were positive, one randomised controlled study found no effective impact on either treatment rates or perinatal mortality reduction (Myer 2003). Indeed, in spite of the presence of laboratory access in some developing areas, the number of infected women treated fully is still in the minority (Wilkinson 1997). Furthermore, in developing countries, useful screening tools such as treponemal tests are often obtainable only at reference laboratories or large regional centres (Peeling 2004). Hence, syphilis screening has been constrained by varying dynamics and largely due to the delays in the identification and treatment of the infected women (Rotchford 2000). Therefore, it is crucial to assess the effectiveness of available screening strategies for the detection of syphilis infection in pregnant women.

Description of the condition

Syphilis is caused by the bacterium Treponema pallidum. The disease manifestation is protean; involvement of any organs in this disease is possible and it may appear with multiple clinical manifestations resulting in a range of severe health outcomes (CDC 2010). Syphilis infection is transmitted via person-to-person direct contact with a syphilis sore, and during vaginal, anal or oral sexual intercourse. The external genitals, vagina, rectum or anus are the main organs where sores usually occur, including lips and inside the mouth. The risk of acquiring HIV infection in an individual with syphilis is two- to five-fold if exposed when an ulcer is present, and consequently, individuals involving in high-risk sexual behavior are likely to suffer from syphilis and HIV co-infection. Furthermore, the syphilis bacterium can be vertically transmitted to the fetus of a pregnant woman who has a syphilis infection; reportedly, at least two-thirds of all newborns are infected from maternal syphilis (Zenker 1990). The likelihood of fetal involvement occurs among women with active syphilis infection (i.e. rapid plasma reagin (RPR) titre greater than 1:4), specifically, insufficient or untreated infection acquired within the five years prior to the pregnancy (Hannah 2011). Sixty-nine per cent of such women with active infection may experience a variety of adverse birth outcomes (Ingraham 1950; McDermott 1993), i.e. late miscarriage (after 16 weeks) or stillbirth in 25% cases, neonatal death at term in 11%, preterm or low birthweight in 13%, and classic symptoms and clinical signs of congenital syphilis in 20% (Ingraham 1950; McDermott 1993; Schmid 2004; Watson-Jones 2002). Classically, newborns with congenital syphilis are severely infected premature infants with marasmus, a pot belly, 'old man faces’ and withered skin (Walker 2001). The severity of the adverse birth outcomes associated with congenital syphilis is usually determined by the length of the maternal infection as well as pregnancy stage. The majority of the pregnant women with syphilis are asymptomatic and so are many infected newborns at the time of their birth (Peeling 2004). Therefore, if not treated immediately, within a few weeks the disease progression can be fatal (CDC 2010).

Description of the intervention

Early detection and administration of appropriate therapies are at the centre of syphilis prevention strategies: undergoing syphilis screening tests at the first antenatal check-up within the first trimester and again in late stage of pregnancy followed by prompt treatment of sero-positive women with a single dose of long-acting penicillin before the second trimester (WHO 2010).

Serologic testing is the core strategy of syphilis screening and diagnosis (Hook 1992; Peeling 2004). The are two main types of serologic tests: non-treponemal tests and treponemal tests. Non-treponemal tests identify antibodies to reagin, a cholesterol-lecithin-cardiolipin antigen that cross-reacts with antibodies present in the sera of patients with syphilis. Non-treponemal tests such as the RPR test are easy to perform, sensitive, and relatively cheap (Peeling 2004). Furthermore, the non-treponemal test is quantitative and treatment response can be followed over time (Fiumara 1978). On the other hand, in most cases, the treponemal tests remain positive indefinitely, whether the person has been treated or not. In addition, treponemal tests, e.g. enzyme immunoassay (EIAs) are more costly than non-treponemal tests and can be difficult to perform (Peeling 2004). Seroprevalence data from antenatal screening programmes are used as one of the proxy indicators for monitoring the prevalence of sexually transmitted infections (Peeling 2004). Non-treponemal tests such as RPR can be performed at a local laboratory but one of the major limitations is that RPR can not be carried out on whole blood. Conversely, confirmatory assays such as EIAs, although useful to obtain prevalence rates and surveillance facts, are usually available only at reference or large regional laboratories in resource-poor settings. Currently, numerous improved sero-diagnostic tools are available for the control and treatment of syphilis. For example, nowadays RPR and Venereal Diseases Research Laboratory test (VDRL) reagents can be stored at room-temperature. In addition, existing solar-energy powered rotators have provided the means to carry out these tests in resource-poor settings where there is a lack of, or no electricity (Peeling 2004). Rapid and easy treponemal tests using whole blood, serum or plasma can be stored at room temperature for six to 12 months, are cost-effective (Peeling 2004), and the performance of some of these tests is comparable to laboratory tests (Fears 2001; Lien 2000). It is noteworthy that syphilis screening and treatment are estimated to be the most cost-effective public health interventions in existence (WHO 2007).

How the intervention might work

Prevention success lies in the early detection of syphilis in pregnant women and prompt treatment management before the second trimester (WHO 2010). As recommended by the WHO, all pregnant women should undergo antenatal syphilis screening tests; however, by some means, women without test results at delivery should also be tested or re-tested. Women should also be well informed about the importance of being tested for HIV infection. Additionally, this treatment should also be offered to their partners and treatment planning should be primed in order to protect their infants at birth. Screening of pregnant women in the early stage of their pregnancy (preferably prior to 24 weeks of gestational age) can substantially avert the burden of associated adverse birth outcomes in many parts of the developing world. Screening pregnant women at the routine antenatal check-up, in the first trimester, and again in the late stage of pregnancy, and finally the prompt treatment of those women detected with syphilis sero-positive results are desirable. Syphilis is curable by administering a single dose of long-acting penicillin, and prevents related consequences in the unborn babies. Either one (primary or secondary disease) or three (latent disease) penicillin doses can be effective to treat maternal syphilis, depending on the disease stage.

Why it is important to do this review

Evidence on the effectiveness of screening strategies for the detection and treatment of maternal syphilis is scarce from randomised controlled trials, and most of the knowledge is derived from observational studies. Moreover, earlier reviews of syphilis screening and treatment detected either no intervention effect on preterm birth reduction (Barros 2010), or high grade of evidence (Menezes 2009). Therefore, this review will attempt to accumulate quality evidence on the effectiveness of syphilis screening strategies in pregnant women and their neonates.

Objectives

To assess the effectiveness of maternal syphilis screening strategies.

Methods

Criteria for considering studies for this review

Types of studies

Randomised (individual and clustered) controlled trials comparing different syphilis screening strategies during routine antenatal check-up will be sought. The unit of randomisation could be either individual pregnant women or any formal healthcare facilities e.g. health posts/clinics. Studies that have been presented only as abstracts will also be included indicating their appropriate status. Cross-over trials and quasi-randomised experimental study designs will be excluded.

Types of participants

The eligible participants will be either pregnant women or healthcare facilities/clinics depending on the randomisation unit in each included trial.

Types of interventions

We plan to examine the effectiveness of syphilis testing strategies offered to pregnant women attending routine antenatal check-up. We will compare available syphilis screening tests versus no screening tests. However, if we find trials that investigate the effect of combined screening strategies, i.e. syphilis and HIV/AIDs screening, we will consider them for inclusion in the subsequent review, if the only difference between the arms was that of syphilis screening strategies.

Types of outcome measures

Primary outcomes
  • Perinatal mortality

  • Coverage of different screening tests for the detection and treatment of syphilis infection

  • Obstacles/challenges in the uptake of antenatal syphilis screening tests

Secondary outcomes
  • Incidence of congenital syphilis

  • Incidence of HIV/AIDs in pregnant women and neonates

  • Any other adverse outcomes reported in the included studies will be summarised

Economic data for the use of healthcare resources
Mothers
  • Antenatal hospital admission

Neonates
  • Special care/intensive care admission

Search methods for identification of studies

Electronic searches

We will contact the Trials Search Co-ordinator to search the Cochrane Pregnancy and Childbirth Group’s Trials Register. 

The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co-ordinator and contains trials identified from:

  1. monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);

  2. weekly searches of MEDLINE;

  3. weekly searches of EMBASE;

  4. handsearches of 30 journals and the proceedings of major conferences;

  5. 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. 

Searching other resources

We will check the studies cited in relevant review articles.

We will not apply any language restrictions.

Data collection and analysis

Selection of studies

Two review authors (S Shahrook (SS) and R Mori (RM)) will independently assess all the potential studies identified from the search methods to be included in the review. Two review authors will obtain the full text of all eligible trials identified by at least one author, and independently review the full copies for eligibility. We will attempt to contact authors of the original studies if we need further clarification for inclusion. We will resolve any disagreement through discussion or, if required, we will consult an arbiter.

Data extraction and management

Data will be extracted using a specified form. For eligible studies, two review authors (SS and RM) will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult an arbiter. 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

SS and RM 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 outcome assessment as:

  • low, high or unclear risk of bias.

(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; missing outcome data balanced across groups);

  • high risk of bias (e.g. numbers 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:

  • low risk of other bias;

  • high risk of other bias;

  • unclear whether there is risk of other 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 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

Dichotomous data

For dichotomous data, we will present results as summary risk ratio with 95% confidence intervals. 

Continuous data

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

Cluster-randomised trials

We will include cluster-randomised trials in the analyses along with individually-randomised trials. To take account of design effect, we will adjust their sample sizes using the methods described in the Handbook 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.

Trials with more than two treatment groups

If trials with more than two intervention groups (multi-arm studies) are identified, only directly relevant arms will be included. If studies with various relevant arms are identified, groups will be combined to generate a single pair-wise comparison (Higgins 2011), and the disaggregated data in the corresponding subgroup category will be included. If the control group is shared by two or more study arms, the control group over the number of relevant subgroup categories will be divided to avoid double counting the participants (for dichotomous data, we will divide the events and the total population, and for continuous data, we will assume the same mean and standard deviation but will divide the total population). The details will be described in the 'Characteristics of included studies' tables.

Cross-over trials

We will not include cross-over trials as they are generally considered to be inappropriate while measuring a primary outcome which is irreversible such as mortality as described in the Cochrane Handbook for Systematic Reviews of Interventions section 16.4.

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 I² is greater than 30% and either T² is greater than zero, 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.  If asymmetry is suggested by a visual assessment, we will perform exploratory analyses to investigate it.

Data synthesis

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

When data are available or appropriate, we plan to carry out the following subgroup analyses.

  1. Low-income versus middle-income countries.

  2. Study settings, i.e. antenatal clinics versus other healthcare facilities.

  3. HIV/AIDs infection status of the pregnant women and neonates.

  4. Syphilis screening strategies including HIV/AIDs versus without HIV/AIDs screening.  

The following outcomes will be used in subgroup analysis.

  • Perinatal mortality.

  • Coverage of different syphilis screening tests.

  • Obstacles/challenges in the uptake of antenatal syphilis screening tests.

We will assess subgroup differences by interaction tests available within RevMan (RevMan 2011).  We will report the results of subgroup analyses quoting the χ2 statistic and p-value, and the interaction test I² value.

Sensitivity analysis

Sensitivity analyses will be performed to assess the risk of bias effects (trials with low or unclear sequence generation and allocation concealment and either high levels of attrition or inadequate blinding) on the analyses. If any cluster-randomised trials are identified and included, sensitivity analysis using a range of ICC values will be carried out. We will carry out sensitivity analysis for primary outcomes only.

Acknowledgements

We are thankful for the support provided by the Cochrane Pregnancy and Childbirth group during the protocol development process.

As part of the pre-publication editorial process, this protocol has been commented on by two peers (an editor and referee who is external to the editorial team), a member of the Pregnancy and Childbirth Group's international panel of consumers and the Group's Statistical Adviser.

Contributions of authors

Sadequa Shahrook drafted the protocol with advice from Rintaro Mori. Tumendemberel Ochirbat and Harumi Gomi assisted in drafting the protocol.

Declarations of interest

None known.

Sources of support

Internal sources

  • National Center for Child Health and Development, Japan.

External sources

  • Ministry of Health, Labour and Welfare, Japan.

Ancillary