Abstract
Background
Maternal caffeine consumption during pregnancy may have adverse effects on fetal, neonatal and maternal outcomes.
Objectives
This review investigates the effects of restricting caffeine intake by mothers on fetal, neonatal and pregnancy outcomes.
Search methods
We searched the Cochrane Pregnancy and Childbirth Group's Trials Register (16 January 2015), scanned bibliographies of published studies and corresponded with investigators.
Selection criteria
Randomised controlled trials (RCTs) including quasi‐RCTs investigating the effect of caffeine and/or supplementary caffeine versus restricted caffeine intake or placebo on pregnancy outcomes.
Data collection and analysis
Two review authors independently assessed trials for inclusion and risk of bias, extracted data and checked them for accuracy.
Main results
Two studies met the inclusion criteria but only one contributed data for the prespecified outcomes. Caffeinated instant coffee (568 women) was compared with decaffeinated instant coffee (629 women) and it was found that reducing the caffeine intake of regular coffee drinkers (3+ cups/day) during the second and third trimester by an average of 182 mg/day did not affect birthweight (g) (mean difference (MD) 20.00, 95% confidence interval (CI) ‐48.68 to 88.68; one study, 1197 participants; low quality evidence), preterm birth (risk ratio (RR) 0.81, 95% CI 0.48 to 1.37; one study, 1153 participants; low quality evidence) or small‐for‐gestational age (RR 0.97, 95% 0.57 to 1.64; one study, 1150 participants). Risk of bias was moderate in both studies.
Two outcomes were assessed and assigned a quality rating using the GRADE methods. Evidence for these two outcomes (birthweight and preterm birth) was assessed as of low quality, with downgrading decisions due to the relatively small sample sizes and the wide confidence interval of the one included trial that contributed data. Neither of the studies reported on any of the other primary outcomes (low birthweight; first trimester fetal loss; perinatal mortality; fetal hypoxia; fetal tachycardia) or on any of the reviews neonatal or maternal outcomes.
Authors' conclusions
There is insufficient evidence to confirm or refute the effectiveness of caffeine avoidance on birthweight or other pregnancy outcomes. There is a need to conduct high‐quality, double‐blinded RCTs to determine whether caffeine has any effect on pregnancy outcome.
Plain language summary
Effects of restricted caffeine intake by mother on fetal, neonatal and pregnancy outcomes
Caffeine is a stimulant found in tea, coffee, cola, chocolate and some over‐the‐counter medicines. Conflicting results found in the literature make it difficult for health professionals to advise pregnant women about avoiding caffeine during pregnancy. Clearance of caffeine from the mother's blood slows down during pregnancy. Some authors of observational studies have concluded that caffeine intake is harmful to the fetus, causing growth restriction, reduced birthweight, preterm birth or stillbirth. The newborn could also have withdrawal symptoms if the mother has a high intake of caffeine (more than eight cups of coffee per day).
Two studies met the inclusion criteria but only one contributed data to the outcomes of interest. The study was based in Denmark. Women less than 20 weeks pregnant were randomly assigned to drinking caffeinated instant coffee (568 women after exclusions) or decaffeinated instant coffee (629 women). Drinking three cups of coffee a day in early pregnancy had no effect on birthweight, preterm births or growth restriction.
Both included studies were randomised controlled trials. One randomly allocated pregnant women to either caffeinated or decaffeinated groups. It was unclear from the other whether allocation concealment was undertaken. Blinding of personnel and study participants was satisfactory in both studies while blinding of outcome assessor was not clearly stated. Attrition bias was also not clearly explained in one study. The results from the one trial that provided data for analysis showed that there was no evidence of an effect of caffeine avoidance on the outcomes birthweight, preterm birth or small‐for‐gestational age.
Two outcomes were assessed and assigned a quality rating using the GRADE methods. Evidence for these two outcomes, namely birthweight and frequency of preterm birth, was assessed as of low quality, with downgrading decisions due in part to the relatively small sample sizes and the wide confidence interval of the one included trial that contributed data.
There is insufficient evidence to confirm or refute the effectiveness of caffeine avoidance on birthweight or other pregnancy outcomes.
Summary of findings
Summary of findings for the main comparison. Caffeinated (experimental group) compared with decaffeinated group (control group) for health problem or population.
| Caffeinated (experimental group) compared to decaffeinated group (control group) for health problem or population | ||||||
| Patient or population: Pregnant women recruited before 20 weeks' gestation Settings: Denmark Intervention: Caffeinated (experimental group) Comparison: Decaffeinated group (control group) | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect (95% CI) | No of Participants (studies) | Quality of the evidence (GRADE) | Comments | |
| Assumed risk | Corresponding risk | |||||
| Decaffeinated group (control group) | Caffeinated (experimental group) | |||||
| Birthweight (g) | The mean birthweight in the control group was 3,519 grams | The mean birthweight (grams) in the intervention group was 20 higher (48.68 lower to 88.68 higher) | MD 20.00 (‐48.68 to 88.68) | 1197 (1 RCT) | ⊕⊕⊝⊝ LOW 1 | The difference in the mean birthweight was not statistically significant, it would also not differ clinically as the birthweight in the intervention group was only 20 g higher. |
| Preterm birth | Study population | RR 0.81 (0.48 to 1.37) | 1153 (1 RCT) | ⊕⊕⊝⊝ LOW 1 | ||
| 52 per 1000 | 42 per 1000 (25 to 71) | |||||
| Moderate | ||||||
| 52 per 1000 | 42 per 1000 (25 to 71) | |||||
| Low birthweight | This outcome was not reported in either study | |||||
| Perinatal mortality rate | This outcome was not reported in either study | |||||
| Sudden infant death syndrome | This outcome was not reported in either study | |||||
| Gestational diabetes | This outcome was not reported in either study | |||||
| *The basis for the assumed risk is the mean reported for the Bech 2007 trial. The corresponding risk (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% confidence intervaI). | ||||||
| GRADE Working Group grades of evidence High quality: Further research is very unlikely to change our confidence in the estimate of effect. Moderate quality: Further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate. Low quality: Further research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate. Very low quality: We are very uncertain about the estimate. | ||||||
1One study included 1153 women. Wide confidence interval crossing the line of no effect (‐2)
Background
Description of the condition
Caffeine is the most commonly used psychoactive substance in the world. It is found in a range of beverages and food, mainly in tea, coffee, cola, chocolate bars and some medications. There has been a concern that maternal consumption of caffeine in pregnancy may be associated with adverse pregnancy outcomes. However, studies investigating antenatal caffeine intake and pregnancy outcomes have had mixed results. Some authors have concluded that caffeine intake is harmful, causing stillbirth and fetal death (Bech 2005), some that it has no effect (Browne 2007), and others claim that it is beneficial in reducing the risk of gestational diabetes mellitus (GDM) (Adeney 2007).
Caffeine, a trimethylxanthine alkaloid, is readily available in coffee (containing from 85 to 110 mg/cup), tea (about 50 mg/cup), cola beverages (30 to 45 mg/serving), cocoa (about 5 mg/cup), chocolate (25 mg/small bar), as well as preservatives, analgesics and other pharmaceutical preparations (Knutti 1982). Caffeine's primary metabolite, paraxanthine, can pass the placental barrier, exposing the fetus to maternally ingested caffeine. Adenosine is an endogenous modulator of neuronal excitability in mammals' central nervous systems. Paraxanthine antagonises adenosine receptors (A1) in materno‐fetal brain and heart inhibit glutamate release in peripheral tissues, which may have a dose‐dependent and cumulative adverse effect on the metabolic activity of both mother and fetus (Gaytan 2006; Grosso 2006; Iglesias 2006).Exposure to caffeine can also lead to vasoconstriction in the uterus and placenta circulation, which may in turn affect fetal growth and development (Bech 2005).
Animal studies have shown that chronic caffeine exposure during pregnancy promotes a decrease in adenosine A1 receptors in both maternal and fetal whole brain, which in turn increases stimulatory activities, making the brain and other tissues vulnerable to the harmful effect of caffeine because there is no blood‐brain barrier or placental barrier to caffeine (Leon 2002). Moreover, clearance of caffeine from the mother's blood slows down during pregnancy and its half life is tripled during the second and third trimester (Knutti 1981), while the fetus is lacking a sufficient amount of the enzyme needed to metabolise it (Aldridge 1979).
Description of the intervention
Pregnant women received caffeinated instant coffee or decaffeinated instant coffee in the randomised controlled studies under investigation in this review. Women were asked to replace their usual coffee with the coffee provided, but were not advised on how much to drink or avoid regular coffee offered by others or intake of other caffeinated beverages such as tea, cocoa, or cola.
How the intervention might work
Maternal consumption of caffeine may possibly affect the pregnancy at any time throughout intrauterine life. Animal studies suggest that caffeine is teratogenic when administered in large amounts (more than eight cups per day), resulting in congenital anomalies, namely oral cleft and cardiovascular malformation (Berger 1988; Bruyere 1987; Elmazar 1982). However, so far, current epidemiological evidence is unable to detect appreciable teratogenic effect of caffeine exposure in the human fetus (Browne 2006).
Excessive maternal caffeine consumption (more than eight cups per day) may result in increased levels of catecholamines in both the mother and fetus, which may lead to utero‐placental vasoconstriction (Kirkinen 1983), increased fetal heart rate and arrhythmias (irregularity of heart rate) (Resch 1983) and, as a consequence, lack of fetal oxygenation. A recent study suggests caffeine impaired insulin sensitivity in women with GDM (Robinson 2009). Thus, it is theoretically plausible that these effects could adversely affect the pregnancy and increase the risk of miscarriage (Tolstrup 1983), low birthweight (Bracken 2003; Klebanoff 2002), stillbirth (Wisborg 2002), and sudden infant death syndrome (Ford 1988). The Rondo study suggested that the proportion of mothers who delivered growth‐restricted babies increased as the average consumption of coffee increased (Rondo 1996). Moreover, neonatal withdrawal symptoms have been observed as a result of high levels of maternal caffeine intake (McGowan 1988).
However, other investigators have failed to find any association between caffeine intake and poor pregnancy outcomes. Wen 2001 showed that pregnant women who were taking coffee before pregnancy had fewer incidents of spontaneous miscarriage. His population‐based prospective study was carried out on a group of 575 women who delivered singleton live births and 75 women who had spontaneous miscarriages. Clausson 2002 in his prospective population‐based cohort study of 953 women showed that there was no association between caffeine consumption and birthweight, gestational age and birthweight ratio. Another large prospective study of 2291 mothers also showed that caffeine consumption in the first and third trimesters was not associated with intrauterine growth restriction, low birthweight or preterm delivery (Bracken 2003).
Beneficial effects of caffeine intake during pregnancy are reported in some other studies. Moderate prepregnancy coffee consumption may have a protective association with GDM (Adeney 2007). It has been found that the consumption of coffee increases ventilatory frequency in the general population (Martinet 2002). A study on rats suggests that caffeine present in drinking fluid of lactating dams (mothers) may prevent ponto‐medullary respiratory disturbances (Bodineau 2006). Moreover, the beneficial effect of caffeine has been shown in neonatal rodents. Caffeine as an adenosine antagonist may prevent brain injures due to lack of oxygen. Therefore, it is postulated that caffeine administration during early postnatal development may prevent brain injury, which is the most common cause of cerebral palsy and cognitive impairment in premature infants (Back 2006).
Why it is important to do this review
Conflicting results found in the literature make it difficult for health professionals to advise pregnant women about avoiding caffeine during pregnancy. The objective of this review, therefore, is to assess the impact of avoidance of maternal consumption of caffeine on pregnancy outcome.
Objectives
To assess the effects of restricted caffeine intake by mother on fetal, neonatal and pregnancy outcomes.
Methods
Criteria for considering studies for this review
Types of studies
Published or unpublished randomised controlled trials, including quasi‐randomised controlled trials and cluster‐randomised trials.
Types of participants
Pregnant women of any age and parity.
Types of interventions
Caffeine intake and caffeine supplements (inclusive of all caffeinated beverages, such as tea and coffee, or non‐beverages, such as chocolate and medications) during pregnancy versus limited use of caffeine or placebo or any other intervention.
Types of outcome measures
Primary outcomes
Fetal outcomes
Birthweight (g).
Low birthweight, a fetus that weighs less than 2500 g (5 lb 8 oz) regardless of gestational age (assessed at time of birth), very low birthweight, which is less than 1500 g, and extremely low birthweight, which is less than 1000 g.
Small‐for‐gestational age (those whose birthweight lies below the 10th percentile for that gestational age, assessed at time of birth).
First trimester fetal loss or miscarriage (natural or spontaneous end of a pregnancy at a stage where the embryo or the fetus is incapable of surviving, generally defined in humans at a gestation prior to 20 weeks).
Perinatal mortality rate per 100,000 inclusive of postnatal death (death of a liveborn infant until 42 days after delivery) and stillbirth (delivery of a dead fetus at 28 weeks' gestation or more).
Fetal hypoxia.
Fetal tachycardia and arrhythmias.
Preterm birth (i.e. the birth of a baby before 37 weeks).
Secondary outcomes
(1) Neonatal outcomes
(1.1) Neonatal caffeine withdrawal syndrome. (1.2) Neonatal apnoea. (1.3) Tachycardia and arrhythmias. (1.4) Cerebral palsy and cognitive impairment. (1.5) Sudden infant death syndrome (a syndrome marked by the symptoms of sudden and unexplained death of an apparently healthy infant aged one month to one year).
(2) Maternal outcomes
(2.1) Headache. (2.2) Nausea. (2.3) Psychological outcomes (such as depression, anxiety, depression, sleepiness or lethargy either self‐reported or objective). (2.4) Gestational diabetes. (2.5) Glucose tolerance in women with or without gestational diabetes mellitus (not a prespecified outcome).
Search methods for identification of studies
The following methods section of this review is based on a standard template used by the Cochrane Pregnancy and Childbirth Group.
Electronic searches
We searched the Cochrane Pregnancy and Childbirth Group’s Trials Register by contacting the Trials Search Co‐ordinator (16 January 2015).
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 (Ovid);
weekly searches of Embase (Ovid);
monthly searches of CINAHL (EBSCO);
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, Embase and CINAHL, 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 scanned bibliographies of published studies and corresponded with investigators.
We did not apply any language or date restrictions.
Data collection and analysis
For methods used in the previous version of this review, seeJahanfar 2013.
Assessment of quality of evidence in included studies
For this update, no new reports were identified for assessment but we assessed the quality of evidence of the existing studies using the GRADE approach (Schunemann 2009) in order to assess the quality of the body of evidence relating to the following outcomes for the main comparison of caffeinated versus decaffeinated group.
Fetal outcomes
1. Birthweight
2. Low birthweight
3. Preterm birth
4. Perinatal mortality rate
Neonatal outcomes
5. Sudden infant death syndrome
Maternal outcomes
6. Gestational diabetes
GRADEprofiler (GRADEpro 2014) was used to import data from Review Manager 5.3 (RevMan 2014) in order to create a ’Summary of findings’ table. A summary of the intervention effect and a measure of quality for each of the above outcomes was produced using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of the body of evidence for each outcome. The evidence can be downgraded from 'high quality' by one level for serious (or by two levels for very serious) limitations, depending on assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates or potential publication bias.
In future updates, if new reports are identified, we will use the methods described in Appendix 1.
Results
Description of studies
Results of the search
Two studies (Bech 2007; Robinson 2009) met the inclusion criteria but only one study (Bech 2007) contributed data for the prespecified outcomes.
Included studies
The study by (Bech 2007) compared drinking caffeinated instant coffee versus decaffeinated instant coffee during pregnancy. Overall, 1207 pregnant women were randomised. After exclusion of 10 participants (due to erroneous serial number, participating twice and second pregnancy), 568 women were randomised to caffeinated instant coffee and 629 to decaffeinated instant coffee. Comparison between these two groups showed only minor differences in baseline characteristics. A total of 1153 women with a live born singleton were included in the analysis of birthweight and length of gestation. Of these, 8.6% (54/629) randomised to the decaffeinated group and 4.9% (28/568) randomised to the caffeinated group dropped out of the study before giving birth. We have included the outcomes of these women in the main analysis.
Main outcomes measured were birthweight and length of gestation. Secondary outcomes included head and abdominal circumference, ponderal index, Apgar score and placenta weight.
We selected those outcomes that matched those specified for our review (mean birthweight, frequency of preterm birth and small‐for‐gestational age) for analysis.
Robinson 2009 studied the effect of acute caffeine ingestion on glucose tolerance in women with or without gestational diabetes mellitus (GDM). The outcome was not relevant to our review.
Excluded studies
None.
Risk of bias in included studies
See Figure 1; and Figure 2 for a summary of ’Risk of bias’ assessments.
1.
'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
2.
'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study.
Allocation
In the Bech 2007 study, randomisation was performed using a central computer. The manufacturer provided coffee in identical boxes without labels. The investigators used a computer‐generated randomisation schedule to allocate women to either group.
In the Robinson 2009 study, methods of sequence generation and allocation concealment were not described. The trial was assessed as being at unclear risk of bias. This study was described as being a "double‐blind, randomized, cross‐over study", but the methods for randomisation and cross‐over were not described. It was not possible to assess whether this was a cross‐over study. Further details have been sought from the authors.
Blinding
Bech 2007 study was double blind as both the project co‐ordinator and the participants were blinded to the type of coffee given to each woman. The data analyser was also blinded until after analysis. Investigators and study participants in Robinson 2009 were reportedly blinded to the order of treatment.
Incomplete outcome data
The drop‐out rate in Bech 2007 study prior to giving birth, was 8.6% (54/629) for the decaffeinated group and 4.9%(28/568) for the caffeinated group. Attrition was not mentioned by Robinson 2009.
Selective reporting
There was insufficient information to judge whether reporting bias was present in the two trials and so they have both been assessed as being at unclear risk of bias (Bech 2007; Robinson 2009)..
Other potential sources of bias
No obvious sources of bias, other than many other sources of dietary caffeine (tea, chocolate, etc) which were not measured in the study (Bech 2007). Women in the decaffeinated coffee group could have increased their caffeine intake from other sources. Robinson 2009 was described as "double‐blind, randomized, cross‐over study", but methods were not clearly described. There was no description of the cross‐over.
Effects of interventions
See: Table 1
One study (Bech 2007) contributed data for analysis.
Caffeinated (experimental group) versus decaffeinated group (control group)
Primary outcomes
The mean birthweight for babies born to women in the caffeinated group was 3539 g (standard deviation (SD) 604 g), compared with 3519 g (SD 607 g) for babies born to women in the decaffeinated group (P = 0.48). There was no significant difference between the two groups (mean difference (MD) 20.00, 95% confidence interval (CI) ‐48.68 to 88.68; participants = 1197) (Analysis 1.1). In the caffeinated and decaffeinated groups, respectively, 4.5% (25/552) and 4.7% (28/598) of infants were born small‐for‐gestational age (risk ratio (RR) 0.97, 95% CI 0.57 to 1.64; participants = 1150) (Analysis 1.3). This difference was not statistically significant.
1.1. Analysis.
Comparison 1 Caffeinated (experimental group) versus decaffeinated group (control group), Outcome 1 Birthweight (grams).
1.3. Analysis.
Comparison 1 Caffeinated (experimental group) versus decaffeinated group (control group), Outcome 3 Small‐for‐gestational age.
In the caffeinated and decaffeinated groups, respectively, 4.2% (23/552) and 5.2% (3.1/601) of infants were born preterm (RR 0.81, 95% CI 0.48 to 1.37; participants = 1153) (Analysis 1.2). This comparison was not found to be statistically significant.
1.2. Analysis.
Comparison 1 Caffeinated (experimental group) versus decaffeinated group (control group), Outcome 2 Preterm birth.
The authors concluded that drinking three cups of coffee per day did not have any effect on birthweight or gestational age. However, they could not rule out that larger reductions in caffeine might increase birthweight.
The only outcomes reported in the trial of interest (Bech 2007) in this review were birthweight, preterm birth and small‐for‐gestational age. As the analysis suggests, a modest reduction in intake during the second and third trimester, by providing decaffeinated coffee to women who drank three or more cups/day early in pregnancy, did not affect birthweight or length of gestation. None of the other prespecified outcomes were included in this trial.
Secondary outcomes
None of the review secondary outcomes were reported in the trial (Bech 2007).
Outcomes not prespecified
Our updated search in January 2010 identified a new study (Robinson 2009). The outcomes presented in this paper (assessment of glucose tolerance in women with or without gestational diabetes mellitus) are not the same as our predefined primary and secondary outcomes. Caffeine intake in Robinson 2009 showed impaired insulin sensitivity in women with GDM. However, the numbers of women randomised to the intervention and control groups were small Analysis 1.4.
1.4. Analysis.
Comparison 1 Caffeinated (experimental group) versus decaffeinated group (control group), Outcome 4 Glucose tolerance ‐ serum Insulin (pmol/L) (not prespecified).
Discussion
Summary of main results
Two studies met the inclusion criteria but only one contributed data for the prespecified outcomes. Caffeinated instant coffee (568 women) was compared with decaffeinated instant coffee (629 women) and it was found that reducing the caffeine intake of regular coffee drinkers (3+ cups/day) during the second and third trimester by an average of 182 mg/day did not affect birthweight (g), preterm birth or small‐for‐gestational age. Neither of the studies reported on any of the other primary outcomes (low birthweight; first trimester fetal loss; perinatal mortality; fetal hypoxia; fetal tachycardia) or on any of the reviews neonatal or maternal outcomes. In summary, there is insufficient evidence to evaluate the effect of caffeine on fetal, neonatal and maternal outcomes.
Overall completeness and applicability of evidence
Evidence is quite scarce. There is not enough evidence to advise pregnant mothers to restrict coffee intake during pregnancy.
Quality of the evidence
Risk of bias was found to be moderate in both studies. Two outcomes were assessed and assigned a quality rating using the GRADE methods. Evidence for these two outcomes (birthweight and preterm birth) was assessed as of low quality, with downgrading decisions due to the relatively small sample sizes and the wide confidence interval of the one included trial that contributed data.
Potential biases in the review process
The review has been updated and no additional reports were identified for assessment. We did not apply any language or date restrictions. We acknowledge that there is the potential for bias at all stages in the reviewing process. We attempted to minimise bias in a number of ways; for example, two review authors independently carried out data extraction and assessed risk of bias. However, we acknowledge that such assessments involve subjective judgments, and another review team may not have agreed with all of our decisions.
Agreements and disagreements with other studies or reviews
Comparative observational studies suggest that caffeine can have a debilitating effect on the natural growth of the fetus, leading to low birthweight (Bracken 2003), growth restriction (Rondo 1996) and even stillbirth (Wisborg 2002). In contrast, other observational studies with cohort study designs and large sample sizes failed to show any association between caffeine intake and poor pregnancy outcomes (Bracken 2003; Clausson 2002). Randomised controlled trials are lacking in this field.
These conflicting results call for properly designed double‐blind randomised controlled trials (RCTs) to establish the possibility of confidently advising women about avoiding caffeine during pregnancy. When assessing the available studies in this review, we were unable to find any study investigating some of the predefined outcomes of this review, such as maternal outcomes or secondary fetal outcomes.
Future studies, incorporating long‐term outcome measures in evaluating caffeine intake during pregnancy, may prove to be difficult or even unethical. It should be noted that in order to evaluate all primary outcomes (including spontaneous abortion, birth defects) an intervention would need to be applied before pregnancy or in very early pregnancy. If enrolment in the trial encourages women who might discontinue coffee consumption, to continue consuming coffee during pregnancy, the intervention would be unethical if a harmful outcome could be anticipated. Furthermore, it is not clear how much caffeine, in which shape or form, with what quality, can cause fetal or maternal debilitating effect, if any.
Authors' conclusions
Implications for practice.
Little evidence is available from the one included randomised controlled trial (RCT) that contributed data for our prespecified outcomes to evaluate the effect of caffeine on fetal, neonatal and maternal outcomes. However, the included trial did not evaluate all of the prespecified outcomes from our review protocol.
Implications for research.
There is a need for high‐quality, properly designed RCTs in this field. Proper randomisation, adequate allocation concealment, blinding of outcome assessors, participants and data analysts and clear attrition policies are crucial to ensure appropriate comparisons between caffeinated and decaffeinated groups. Various outcome measurements including fetal and maternal outcomes should be considered in future studies. We recommend a comprehensive RCT to investigate all of the primary and secondary outcomes suggested in our review protocol.
What's new
| Date | Event | Description |
|---|---|---|
| 14 January 2015 | New search has been performed | Search updated. No new reports identified. A 'Summary of findings' table has been incorporated. |
| 14 January 2015 | New citation required but conclusions have not changed | Review updated. |
History
Protocol first published: Issue 1, 2008 Review first published: Issue 2, 2009
| Date | Event | Description |
|---|---|---|
| 29 November 2012 | New citation required but conclusions have not changed | Review updated. |
| 31 October 2012 | New search has been performed | Search updated. No new trials found. |
| 18 January 2012 | Amended | Contact details updated. |
| 20 January 2010 | New search has been performed | Search updated. One new study identified (Robinson 2009). |
| 12 November 2008 | Amended | Converted to new review format. |
Acknowledgements
We would like to acknowledge the contributions of the SEA‐ORCHID group and members of the Cochrane Australasian Centre to the first version of this review (Jahanfar 2013).
We would like to thank Nasreen Aflaifel for her support in the creation of the 'Summary of findings' table for the 2015 update. Nasreen Aflaifel's work was financially supported by the UNDP/UNFPA/UNICEF/WHO/World Bank Special Programme of Research, Development and Research Training in Human Reproduction (HRP), Department of Reproductive Health and Research (RHR), World Health Organization. The named authors alone are responsible for the views expressed in this publication.
This project was supported by the National Institute for Health Research, via Cochrane Infrastructure funding to Cochrane Pregnancy and Childbirth. The views and opinions expressed therein are those of the authors and do not necessarily reflect those of the Systematic Reviews Programme, NIIHR, NHS or the Department of Health.
Appendices
Appendix 1. Methods to be used in future updates
The following methods section of this review is based on a standard template used by the Cochrane Pregnancy and Childbirth Group.
Selection of studies
Two review authors will independently assess for inclusion all the potential studies identified as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will consult a third person.
Data extraction and management
We will design a form to extract data. For eligible studies, two review authors will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult a third person. Data will be entered into Review Manager software (RevMan 2014) and checked for accuracy.
When information regarding any of the above is unclear, we plan 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). Any disagreement will be resolved 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 assessed 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 were at low risk of bias if they were blinded, or if we judged that the lack of blinding 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 could have been supplied by the trial authors, we plan to 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 had about other possible sources of bias.
(7) Overall risk of bias
We will make explicit judgements about whether studies were at high risk of bias, according to the criteria given in the Handbook (Higgins 2011). With reference to (1) to (6) above, we plan to assess the likely magnitude and direction of the bias and whether we considered 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.
Assessment of the quality of evidence in included studies
For future updates the quality of the evidence will be assessed using the GRADE approach (Schunemann 2009) in order to assess the quality of the body of evidence relating to the following outcomes for the main comparison of caffeinated versus decaffeinated group:
Fetal outcomes
1. Birthweight 2. Low birthweight 3. Preterm birth 4. Perinatal mortality rate
Neonatal outcomes
5. Sudden infant death syndrome
Maternal outcomes
6. Gestational diabetes
GRADE profiler (GRADEpro 2014) will be used to import data from Review Manager 5.3 (RevMan 2014) in order to create ’Summary of findings’ tables. A summary of the intervention effect and a measure of quality for each of the above outcomes will be produced using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of the body of evidence for each outcome. The evidence can be downgraded from 'high quality' by one level for serious (or by two levels for very serious) limitations, depending on assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates or potential publication bias.
Measures of treatment effect
Dichotomous data
For dichotomous data, we will present results as summary risk ratio with 95% confidence intervals.
Continuous data
We will use the mean difference if outcomes were measured in the same way between trials. We will use the standardised mean difference to combine trials that measured the same outcome, but used 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 sample sizes or 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.
Cross‐over trials
We will not include cross‐over designs.
Dealing with missing data
For included studies, we will note levels of attrition. If more eligible studies are included, 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, that is, we will attempt to include all participants randomised to each group in the analyses. 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 Tau², I² and Chi² statistics. We will regard heterogeneity as substantial if an I² is greater than 30% and either a Tau² is greater than zero, or there is a low P value (less than 0.10) in the Chi² test for heterogeneity. If we identify substantial heterogeneity (above 30%), we plan to explore it by pre‐specified subgroup analysis.
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 2014). 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 to be 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 Tau² 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, we will use random‐effects analysis to produce it.
We will carry out subgroup analyses based on babies' gender, and singleton or twin pregnancy. We will then further conduct subgroup analysis for twin pregnancies based on chorionicity (mono‐chorion or di‐chorion). These outcomes are considered as confounders on birthweight and adverse fetal outcomes such as fetal loss (e.g. miscarriage, stillbirth) and preterm birth.
We will assess subgroup differences by interaction tests available within RevMan (RevMan 2014). We will report the results of subgroup analyses quoting the Chi² statistic and P value, and the interaction test I² value.
Sensitivity analysis
We plan to carry out sensitivity analyses to explore the effect of trial quality assessed by concealment of allocation, high attrition rates, or both, with poor quality studies being excluded from the analyses in order to assess whether this makes any difference to the overall result.
Data and analyses
Comparison 1. Caffeinated (experimental group) versus decaffeinated group (control group).
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
|---|---|---|---|---|
| 1 Birthweight (grams) | 1 | 1197 | Mean Difference (IV, Fixed, 95% CI) | 20.00 [‐48.68, 88.68] |
| 2 Preterm birth | 1 | 1153 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.81 [0.48, 1.37] |
| 3 Small‐for‐gestational age | 1 | 1150 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.97 [0.57, 1.64] |
| 4 Glucose tolerance ‐ serum Insulin (pmol/L) (not prespecified) | 1 | 27 | Mean Difference (IV, Fixed, 95% CI) | 38.8 [13.57, 64.03] |
Characteristics of studies
Characteristics of included studies [ordered by study ID]
Bech 2007.
| Methods | Randomised: method of randomisation is mentioned as central computer randomisation. Double blind: yes. It was mentioned that participants and study co‐ordinator were both blinded. Data analyst was also blinded until end of data analysis. Follow‐up is described: done on weeks 20, 25, 32 and 4 weeks after expected delivery. 8.6% of participants in decaffeinated group and 4.9% of participants in the caffeinated group dropped out before giving birth. |
|
| Participants | Overall, 1207 pregnant women were randomised. 10 participants were excluded (due to erroneous serial number, participating twice and second pregnancy); 568 women were randomised to caffeinated instant coffee and 629 to decaffeinated instant coffee. A total of 1153 women with a live born singleton were included in the analysis of birthweight and length of gestation. Of these, 8.6% (54/629) randomised to the decaffeinated group and 4.9% (28/568) randomised to the caffeinated group dropped out of the study before giving birth. Inclusion criteria: Danish‐speaking women at less than 20 weeks' gestation who drank 3 cups of coffee per day. Those with history of low birthweight baby (< 2500 g), preterm deliveries, kidney disease, epilepsy, diabetes, or metabolic disorders were excluded from the study. |
|
| Interventions | Taking 3 cups of decaffeinated instant coffee (an average of 62 mg/day) versus the same quantity of caffeinated instant coffee. | |
| Outcomes | Mean birthweight and length of gestational age were considered as the main outcomes. Length, head circumference, abdominal circumference, placenta weight, and Apgar score were secondary outcomes; these are not referenced in this review as they did not fit our objective. | |
| Notes | This study was done between April 1996 and April 1998 in the Department of Obstetrics, Aarhus University Hospital, Denmark. | |
| Risk of bias | ||
| Bias | Authors' judgement | Support for judgement |
| Random sequence generation (selection bias) | Low risk | Women randomised to receive decaffeinated or caffeinated coffee. Completed using computerised randomisation. |
| Allocation concealment (selection bias) | Low risk | Women were allocated to either group by a computer‐generated randomisation schedule and assigned balanced serial numbers of six. Staff labelled coffee boxes with serial numbers according to the randomised schedule. |
| Blinding of participants and personnel (performance bias) All outcomes | Low risk | Project co‐ordinator and participants were blinded to the type of coffee. |
| Blinding of outcome assessment (detection bias) All outcomes | Low risk | Data analyser was also blinded until after analysis. |
| Incomplete outcome data (attrition bias) All outcomes | Low risk | Only 8.6% (54/629) participants from the decaffeinated group and 4.9% (28/568) from the caffeinated group dropped out of the study. |
| Selective reporting (reporting bias) | Unclear risk | Not clear. |
| Other bias | Unclear risk | There are many other sources of dietary caffeine (tea, chocolate, etc) which were not measured in the study. Women in the decaffeinated coffee group could have increased their caffeine intake from these other sources. |
Robinson 2009.
| Methods | Described as a "double‐blind, randomized, cross‐over study" ‐ but methods not clearly described. No details regarding the cross‐over. Women with negative GDM test were assigned to control group (n = 19) and women with an initial positive GDM screen were assigned to the experimental group (n = 8). Within the control and the GDM group, women underwent two further fastings at approximately 28 to 29 weeks and 29 to 30 weeks' gestation (one week apart). Treatments were randomised, and investigators and study participants were blinded to the order of the treatments. | |
| Participants | Pregnant women were referred to obstetric clinics between 24‐28 weeks of gestation and underwent GDM testing for screening. | |
| Interventions | Following an overnight fasting, women ingested caffeine (3 mg/kg pre‐pregnancy body weight) with 250 mL of water, equivalent of 1‐2 cups of coffee) or an identical‐appearing placebo (gelatin) capsule with the same amount of water. | |
| Outcomes | One hour after caffeine or gelatin intake a 75 g 2‐hour oral glucose tolerance test was taken. Insulin, C‐Peptide, proinsulin, free fatty acids, epinephrine and methylxanthines were also measured. | |
| Notes | ||
| Risk of bias | ||
| Bias | Authors' judgement | Support for judgement |
| Random sequence generation (selection bias) | Unclear risk | Women were randomised to receive caffeine or gelatin capsule. No details of method for sequence generation. |
| Allocation concealment (selection bias) | Unclear risk | Those who had an initial 50 g glucose screen (1‐hour glucose value < 7.8 mmol/L) were assigned to the control group. Women with an initial positive 50 g glucose screen were assigned to GDM group if they also had two or more glucose values greater than 5.3 mmol/L (fasting), 10.6 mmol/L (1h), or 8.9 mmol/L (2h) on a subsequent 75 g fasting OGTT. A 1‐hour glucose value of > 10.3 mmol/L after a 50 g glucose was also considered diagnostic for GDM. Within the control group and the GDM group, women underwent two further 75 g fasting OGTTs at approximately 28 to 29 and 29 to 30 weeks' gestation (i.e., one week apart). No information regarding allocation concealment. |
| Blinding of participants and personnel (performance bias) All outcomes | Low risk | Investigators and study participants were blinded to the order of treatment. |
| Blinding of outcome assessment (detection bias) All outcomes | Unclear risk | Not reported. |
| Incomplete outcome data (attrition bias) All outcomes | Unclear risk | Attrition is not mentioned. |
| Selective reporting (reporting bias) | Unclear risk | Reporting bias is not clear. |
| Other bias | Unclear risk | Described as "double‐blind, randomized, cross‐over study" ‐ but methods not clearly described. No description of the cross‐over. |
GDM: gestational diabetes mellitus OGTT: oral glucose tolerance test
Differences between protocol and review
Methods have been updated to the current standard methods text for Cochrane Pregnancy and Childbirth. A 'Summary of findings' table has been incorporated.
Serum Insulin (pmol/L), was added as an outcome in the 2010 update.
Contributions of authors
Dr Shayesteh Jahanfar (SJ) is guarantor for the review. She wrote the first draft of the protocol and revised it in response to editorial feedback. For the first version of the review, she assessed studies for inclusion; assessed trial quality; extracted and analysed data; wrote the first draft of the review and made revisions in response to editorial feedback. SJ prepared the 2015 update,
Dr Halimah Sharifah (HS) provided general comments on the protocol. For the first version of the review, she assessed studies for inclusion; assessed trial quality; extracted data; and commented on the drafts. HS commented and approved the 2015 update.
Sources of support
Internal sources
No sources of support supplied
External sources
-
This review was supported by SEA‐ORCHID, Malaysia.
SEA‐ORCHID provided us with consultation, training workshops and advice. Special thanks to Prof Jackie Ho for her encouragement.
UNDP/UNFPA/UNICEF/WHO/World Bank Special Programme of Research, Development and Research Training in Human Reproduction (HRP), Department of Reproductive Health and Research (RHR), World Health Organization, Switzerland.
Declarations of interest
None known.
New search for studies and content updated (no change to conclusions)
References
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