Methods for blood loss estimation after vaginal birth

  • Protocol
  • Intervention



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

The aim of this systematic review is to evaluate alternative methods for blood loss estimation during the third stage of labour compared with visual estimation for the purpose of reducing the adverse consequences of postpartum haemorrhage after vaginal birth.


Some 358,000 women die each year in childbirth, mostly in developing countries (WHO 2010). Severe bleeding in the postpartum period is the single most important cause of maternal deaths worldwide (AbouZahr 2003; Khan 2006). More than half of all maternal deaths occur within 24 hours of giving birth, most commonly from excessive blood loss. Depending on the rate of blood loss and other factors such as pre-existing anaemia, untreated postpartum haemorrhage (PPH) can lead to hypovolaemic shock, multi-organ dysfunction and maternal death within two to six hours. As it is stated in the most recent edition of Confidential Enquiries into Maternal Deaths in the United Kingdom (Lewis 2011), during 2006 to 2008 there were nine direct maternal deaths from obstetric haemorrhage, including one associated with a uterine rupture. These nine direct deaths from obstetric haemorrhage represent a decline from the 14 that occurred during 2003 to 2005, where a rate of 0.66 per 100,000 maternities (95% confidence interval 0.39 to 1.12) was reported (P = 0.2). Consequently, this triennium, obstetric haemorrhage is reduced to being the sixth leading cause of direct maternal deaths and the mortality rate is the lowest since the UK-wide Confidential Enquiry Reports began in 1985 (Lewis 2011).

Description of the condition

The third stage of labour refers to the period between the birth of the baby and complete expulsion of the placenta and membranes. Blood loss during this period and immediately thereafter depends on how well the placenta separates from the uterine wall and how well the uterus contracts to close the vascular channels in the placenta bed. Other causes of PPH include vaginal or cervical tears, uterine rupture, retained placenta or membranes, abnormal adherence of the placenta or altered homeostasis. Moderate loss of blood is physiological and unlikely to lead to later problems except for women who are already anaemic. The major complication associated with this stage is PPH. This is not necessarily excessive bleeding, and according to the World Health Organization (WHO), PPH is defined as bleeding from the genital tract in excess of 500 mL after the delivery of the baby (WHO 2000). Alternative cut-off points of 600 mL (Beischer 1986) and 1000 mL (Burchell 1980) have also been suggested. This difference in criteria may be due to the classification of blood loss, as blood loss between 500 mL to 1000 mL is considered moderate and over 1000 mL is defined as severe. Globally, this complication occurs in approximately 6% of all deliveries although the prevalence is disproportionately higher in low-income countries (Carroli 2008). However, variations in the estimated incidence of PPH between 5% and 18% have been reported (Gilbert 1987; Hall 1985), even within a single country like the UK, where PPH remains an important cause of maternal mortality (DoH 2004; Gilbert 1987; Hall 1985).

Nearly all maternal deaths (99%) occur in the developing world (Kwast 1991), where other factors, such as infection (especially HIV infection), poor nutritional status and lack of easy access to treatment, may contribute to death in the presence of severe PPH. Many more women survive and suffer serious illness as a result, not only from the effects of acute anaemia (including Sheehan’s syndrome (a postpartum condition where there is decreased functioning of the pituitary gland resulting from uterine haemorrhage during and after childbirth)), but also from the interventions which a severe haemorrhage may necessitate (such as general anaesthesia, manual removal of the placenta, blood transfusion, hysterectomy). Delay in the diagnosis and treatment of PPH may result from an underestimation of blood loss at delivery, among other causes such as lack of resources or clinical skills to resolve the problem. Assessment of postpartum blood loss, particularly after vaginal birth, is recognised as difficult. Many studies found that visual estimates of peripartum blood loss are often inaccurate (Bose 2006; Didly 2004; Duthie 1991; Newton 2000; Prasertcharoensuk 2000; Razvi 1996; Stafford 2008), showing an overestimation of blood loss of low volumes and an underestimation of larger volumes, the magnitude of underestimation typically increasing with the volume of haemorrhage (Zhang 2010).

Description of the intervention

The current worldwide standard practice of postpartum blood loss assessment is visual estimation of blood loss (VEBL). A healthcare provider generally observes the amount of blood lost during delivery and makes a quantitative or semi-quantitative estimate. Methods to quantitatively estimate postpartum vaginal blood loss include, direct collection and measurement or weighing, venous blood sampling, dye dilution techniques for plasma volume measurement, and red blood cell and plasma volume determinations using radioactive tracer elements. The most accurate measures include venous blood sampling for determination of haemoglobin (Hb) concentration, with and without assessment of blood volume by red blood cell labelling or spectrometry. However, these methods have not been widely adopted because they are neither practical nor affordable in most clinical settings (Patel 2006).

A compensated shock occurs with a blood loss of less than 1000 mL and no change or slight change in clinical signs. Substantial changes in heart rate and blood pressure would be seen after a blood loss of more than 1000 mL. Hypotension with significant tachycardia and a rise in respiratory rates would occur after a loss of 25% to 35% of blood volume and profound shock occurs after a 40% blood loss. However, the use of clinical signs may lack accuracy in the assessment of hypotension and needs further testing in order to help guide the management of PPH. In a recently published systematic review of the relationship between blood loss and clinical signs, the shock index was found to be an accurate indicator of compensatory changes in the cardiovascular system due to blood loss (Pacagnella 2013). The shock index is calculated as the heart rate divided by the systolic blood pressure and this simple calculation may transform unstable parameters into a more accurate predictor of hypovolaemia. In addition, the shock index has been recently suggested as a tool to predict mortality due to hypovolaemic shock in trauma patients. The use of the shock index in the early identification and assessment of bleeding is considered promising even in obstetric populations. Considering that most of the evidence included in the systematic review by Pacagnella et al is derived from studies in non-obstetric populations, further studies on the use of the shock index in obstetric populations are needed.

How the intervention might work

We are evaluating alternative methods for blood loss estimation compared with visual estimation, not in terms of their diagnostic accuracy but for their effectiveness in reducing the adverse consequences of both mild and severe PPH. An effective method should not underestimate the amount of blood loss, hence the appropriate therapeutic measures are not applied timely, and also not overestimate it, leading to unnecessary and potentially aggressive or invasive treatments.

Potential adverse effects

We will assess the potential side effects of those invasive methods that include blood extraction for any measurement or the injection of any substance to be measured for the quantification of blood loss.

Why it is important to do this review

The consequences of severe PPH are widely known. So too is the importance of finding the most accurate method to quantify blood loss during the third stage of labour in order to prevent or, once commenced, to control PPH. Precision is not the only quality the method should have; it also has to be practical and accessible for all, including minimally trained, healthcare providers.


The aim of this systematic review is to evaluate alternative methods for blood loss estimation during the third stage of labour compared with visual estimation for the purpose of reducing the adverse consequences of postpartum haemorrhage after vaginal birth.


Criteria for considering studies for this review

Types of studies

Randomised controlled trials (full text and abstract) comparing methods for blood loss estimation during the third stage of labour. Quasi-randomised trials and cross-over trials will be excluded.

Types of participants

Pregnant women during third stage of labour and 24 hours post delivery, regardless of other aspects of third stage of labour management and mode of vaginal delivery (spontaneous or instrumental). Women delivering by caesarean section will be excluded.

Types of interventions

Any method for blood loss estimation compared with an alternative.

Types of outcome measures

Studies will be included in the review whether or not they report the following outcome measures of interest.

Primary outcomes
  • Postpartum anaemia (defined as a haemoglobin (Hb) lower than 9 mg/dL)

  • Severe morbidity (including coagulopathy, organ failure, intensive care unit admission)

Secondary outcomes
Maternal outcomes
  • Blood loss greater than 1000 mL

  • Blood loss greater than 500 mL

  • Blood transfusion

  • Use of plasma expanders

  • Use of therapeutic uterotonics

  • Changes in vital parameters such as heart rate, blood pressure, urine output, etc

  • Further operative procedures (curettage, laparotomy, laparoscopy, surgical exploration, manual removal of the placenta, etc)

  • Hysterectomy for postpartum haemorrhage (PPH)

  • Infection

  • Maternal pre- and postdelivery change in Hb concentration

  • Maternal death

Adverse effects
  • Any side effect related to the method used (example phlebitis at the site of puncture for blood extraction)

Acceptability of intervention
  • Maternal dissatisfaction with intervention (as defined by authors)

  • Providers' dissatisfaction with intervention (as defined by authors)

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 search the reference lists of retrieved studies.

We will not apply any language restrictions.

Data collection and analysis

Selection of studies

Two review authors (V Diaz (VD) and E Abalos (EA)) will independently assess for inclusion all the potential studies we identify as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will consult the third review author (Guillermo Carroli (GC)).

Data extraction and management

We will design a form to extract data. For eligible studies, two review authors (VD and EA) will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult the third review author (GC). We will enter data into Review Manager software (RevMan 2012) 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 (VD and EA) 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 (GC).

(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; missing data for less than 20% of participants);

  • 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. 

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. We will adjust their standard errors using the methods described in the Handbook [Section 16.3.4 or 16.3.6] 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 sensitivity or subgroup analysis to investigate the effects of the randomisation unit. 

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 I² is greater than 30% and either the 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 2012). 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 95% confidence intervals, 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.

  1. Whether or not intervention is part of AMTSL (Active management of third stage of labour).

  2. Whether or not oxytocin was used during first stage of labour.

  3. Whether or not an uterotonic was used for prevention of PPH.

  4. Whether or not prevention of PPH with oxytocin was given as intravenous bolus or infusion, or by intramuscular route.

The following outcomes will be used in subgroup analysis.

  1. Severe PPH (at least 1000 mL).

  2. Serious maternal morbidity (organ failure, coma, intensive care unit admission, hysterectomy or as defined by the authors).

We will assess subgroup differences by interaction tests available within RevMan (RevMan 2012). We will report the results of subgroup analyses quoting the χ2 statistic and p-value, and the interaction test I² value.

Sensitivity analysis

We will carry out sensitivity analyses to explore the effect of trial quality on the primary outcomes of this review. Trials will be divided into groups according to whether they are at low risk of bias as opposed to unclear or high risk of bias for the primary outcomes in the review (e.g. inadequate allocation concealment or lost to follow-up in the intervention versus control arms). For cluster-randomised trials, we will perform sensitivity analysis using a range of values for intra-cluster correlation coefficients (ICC).


As part of the pre-publication editorial process, this protocol has been commented on by three peers (an editor and two referees who are external to the editorial team) and the Group's Statistical Adviser.

The National Institute for Health Research (NIHR) is the largest single funder of the Cochrane Pregnancy and Childbirth Group. The views and opinions expressed therein are those of the authors and do not necessarily reflect those of the NIHR, NHS or the Department of Health.

Contributions of authors

Diaz V, Abalos E and Carroli G prepared the protocol. Diaz V is the guarantor for the review.

Declarations of interest

None known.