Scolaris Content Display Scolaris Content Display

Cochrane Database of Systematic Reviews Protocol - Intervention

Positioning for lumbar puncture in newborn infants

Authors' declarations of interest

Version published: 18 January 2023 Version history

https://doi.org/10.1002/14651858.CD015592

This is not the most recent version

view the current version 14 December 2023
Collapse all Expand all

Abstract

Objectives

This is a protocol for a Cochrane Review (intervention). The objectives are as follows:

To assess the success rate of the lateral decubitus, sitting and prone positions for lumbar puncture in newborn infants.

Background

Description of the condition

Lumbar puncture is a procedure to collect a small amount of cerebrospinal fluid (CSF) that surrounds the brain and spinal cord, primarily for diagnostic purposes. The most common indication for lumbar puncture in newborns is suspected sepsis and meningitis, caused by i.e. Streptococcus group B, Escherichia coli, herpes simplex virus, and congenital syphilis. The other indications are seizures of unknown origin and suspected metabolic disease. The lumbar puncture results are essential for the choice and duration of treatment. Lumbar puncture is an invasive procedure that causes pain and discomfort in newborns. The success rate of the procedure varies between 50% to 60% (Bedetti 2021; Neal 2017; Pinheiro 1993). The aspiration needle is inserted into the subarachnoidal space of the spinal cord, usually through the fourth lumbar intervertebral space.

Description of the intervention

The most commonly used positions for lumbar puncture are the lateral decubitus and sitting position; the use of the prone position has also been reported. The position for lumbar puncture has not been yet standardized and remains at the physician's disposal. It is unclear whether the success rate is dependent on the positioning of the infant (sitting versus lateral decubitus versus prone), stylet removal (early versus late), or the experience of the physician. Some neonatologists prefer to have a newborn in the lateral position as it appears to enable stability when holding the infant. On the other hand, in the sitting position, the intervertebral space becomes wider, which might enable a higher success rate for lumbar puncture. However, it requires more effort to have a stable position for the infant during the procedure. The prone position is seldom used in neonates, even though it is considered to be the most comforting position for preterm newborns (Çakıcı 2020).

Regardless of the choice of the position for lumbar puncture, the safety and simplicity of this procedure are warranted in this age group, particularly considering the vulnerability of sick preterm infants. In adults, the maximal hip flexion leads to a higher interspinal distance and facilitates the procedure (Sandoval 2004). To increase the intraspinal space, the assistant keeps the newborn in the desired lumbar puncture position throughout the procedure and checks for the stability of the baby's vital signs. After assessing for contraindication, such as active bleeding, thrombocytopenia, severe cardio‐respiratory instability, uncontrollable seizures, signs of severe intracranial hypertension and skin infection at the lumbar puncture site, the procedure can be started. A sterile field is prepared. The intervertebral space between the fourth lumbar vertebra (L4) and L5 is preferred (Barson 1970; Tubbs 2004). It has been shown that, even in neonates, Tuffier’s line is helpful to determine the point of needle insertion caudal to the termination of the spinal cord and at L4 to L5 intraspinal space in the neonate in the prone position, or at the upper edge of L5 in the laterally flexed position (Van Schoor 2014). A spinal needle with a stylet is slowly advanced into the fourth lumbar intervertebral space with a slight inclination towards the umbilicus for some millimeters until a fall in resistance is felt (Atlas of Procedures in Neonatology 2007). The stylet is then removed and the CSF is collected in vials. The choice of needle size for newborns usually varies between 20 G and 25 G, and smaller needles have been linked to a lower chance of traumatic lumbar puncture (Flett 2020). There are also two different techniques for stylet removal: early, when stylet is removed after three crossing epidermis and dermis levels; and late, where stylet is removed once in breakthrough into the CSF space.

How the intervention might work

Each of the three positions ‐ lateral decubitus, sitting, and prone ‐ has pros and cons (Öncel 2018). One of the main advantages of the lateral decubitus position is better control of the endotracheal tube in intubated neonates and perhaps easier identification of Tuffier's line, i.e. the horizontal line connecting the highest points of the iliac crests. The sitting position gives the best visualization of the intervertebral spaces, which facilitates correct insertion of the needle. In intubated neonates it is difficult to control the endotracheal tube and maintain a stable sitting position, particularly if the assistant is inexperienced. Flexing the hips in both the sitting and the lateral decubitus positions can help to increase the interspinal space width. A study in 2013 evaluated the interspinal width in a population of preterm neonates with a weight < 2500 g; namely that there was a difference between lateral and sitting position. This difference was defined as the interspinal space in infants in the lateral decubitus with the body stretched the narrowest (3.18 mm) compared with the width of (3.445 mm) in a lateral flexed position. In sitting position the intraspinal space was found to be 3.86 mm without hip flexion, being as wide as 4.08 mm with hip flexion (Öncel 2013). Similar results with wider interspinal spaces in sitting flexed position compared with lateral decubitus, with or without hip flexion, have been documented in a population of slightly older and bigger neonates (Oulego‐Erroz 2014). However, the flexion of the hip to obtain the maximum intraspinal space may be uncomfortable and stressful for the neonate, causing a struggle to maintain a stable position and thereby increasing the risk for lumbar puncture failure. Furthermore, passive flexion may lead to instability of vital signs and cardiorespiratory depression. The prone position seems to be the most physiological and comfortable for the neonate, and perhaps the easiest for the assistant holding the baby. The prone position has been demonstrated to provide the best comfort to newborns while promoting sleep at rest (Grunau 2004), and also gives a certain level of stress‐relief during procedures causing pain (Kahraman 2017). However, it may be difficult to perform the lumbar puncture in the prone position in neonates with higher body weight, due to difficulties in identifying the anatomical landmarks.

Furthermore, it is believed that the removal of the stylet may influence the success of the procedure (Baxter 2006). In early stylet removal, there is less risk of penetrating into the internal vertebral venous plexus space, because as soon as the spinal needle enters the intraspinal space there is immediate reflux of CSF. However, if the stylet is removed too early, before passing through the dermis, there is a risk of introducing epidermal cells into the intraspinal space, leading to the formation of epidermoid tumors (Batnitzky 1977; Öncel 2018).

Independently of the position and stylet removal, the lumbar puncture procedure has several risks due to its invasive nature. It is often associated with some minor complications, such as localized pain and post‐lumbar puncture headache, which newborn infants may fail to express or which caregivers may have some difficulties understanding. Major complications include infection, bleeding into the spinal canal, leakage of CSF, and very rarely damage to the spinal cord and cerebral herniation (Öncel 2018).

Why it is important to do this review

Approximately one in two lumbar puncture procedures fails (Bedetti 2021; Neal 2017; Pinheiro 1993). This has detrimental consequences for the management of the newborn infant, e.g. to define the duration and type of antibiotic therapy, and the duration of hospital stay. Moreover, it exposes the infant, one or more times, to an unsuccessful procedure that is known to be painful. This may result in both short‐ and long‐term negative consequences (Walker 2019; Williams 2020), and cause circulatory instability and potentially intraventricular hemorrhage or need for re‐intubation (Atlas of Procedures in Neonatology 2007). Therefore, maximizing the success rate of lumbar puncture is highly relevant. The most effective pharmacological intervention for pain and discomfort management during lumbar puncture is to be assessed in a separate Cochrane Review (Pessano 2022).

Objectives

To assess the success rate of the lateral decubitus, sitting and prone positions for lumbar puncture in newborn infants.

Methods

Criteria for considering studies for this review

Types of studies

We will include prospective randomized controlled trials (RCTs), quasi‐RCTs, cluster‐RCTs, and cross‐over RCTs.

Types of participants

We will include preterm and term infants of postmenstrual age (PMA) up to 46 weeks and 0 days, irrespective of their gestational age at birth, undergoing lumbar puncture for any indication.

Types of interventions

  • Lateral decubitus position versus sitting position

  • Lateral decubitus position versus prone position

  • Sitting position versus prone position

Types of outcome measures

Outcome measures do not form part of the eligibility criteria.

Primary outcomes

  • Successful lumbar puncture procedure at the first attempt, with < 500 to 1000 red blood cells/mm3 (Greenberg 2008)

  • Total number of lumbar puncture attempts

  • Episodes of bradycardia, defined as a fall in heart rate of more than 30% below the baseline or less than 100 beats per minute for 10 seconds or longer

Secondary outcomes

  • Time to perform the lumbar puncture

  • Episodes of desaturation, defined as a decrease of arterial oxygen saturation (SpO2) to less than 80%, with no minimum duration specified

  • Apnea: number of episodes (defined as interruption of breathing for more than 20 seconds) during the procedure

  • Apnea: number of infants with one or more episodes (defined as interruption of breathing for more than 20 seconds) during the procedure

  • Need for pain/sedation medication to perform the lumbar puncture

  • Skin changes at the lumbar puncture site, including bleeding and petechiae

  • Infection rate related to the lumbar puncture

  • Pain, assessed with the following scales:

    • ABC (Acuteness of the first cry, Burst rhythmicity and temporal Constancy of cry intensity) scale (Bellieni 2005); for both term and preterm infants;

    • Behavioral Indicators of Infant Pain (BIIP) (Holsti 2008); for preterm infants only;

    • Douleur Aiguë du Nouveau‐né (DAN) (Acute Pain in Newborn infants, APN, English version) (Carbajal 1997); for both term and preterm infants;

    • Neonatal Infant Pain Scale (NIPS) (Lawrence 1993); for both term and preterm infants;

    • Neonatal Pain, Agitation, and Sedation Scale (N‐PASS) (Hummel 2008); for both term and preterm infants;

    • Premature Infant Pain Profile (PIPP) /PIPP‐revised (PIPP‐R) (Gibbins 2014; Stevens 1996) for both term and preterm infants;

    • Neonatal Facial Coding System (NFCS) for both term and preterm infants (Peters 2003); and

    • Face, Legs, Activity, Cry and Consolability (FLACC) for term infants only (Merkel 1997).

  • Parent satisfaction with care provided in the NICU (as measured by a validated instrument/tool) (Butt 2013)

If a study reports more than one pain scale amongst those specified above, we will report them separately. We plan to report the mean values of each pain scale assessed:

  • during the procedure;

  • up to 10 minutes after the procedure;

  • between 11 and 59 minutes; and

  • at one to two hours after the procedure.

If a study reports more than one time point amongst those specified above, we will report them all. We will report the worst score within each timeframe.

Search methods for identification of studies

The Cochrane Sweden Information Specialist developed a draft search strategy for PubMed (National Library of Medicine) in consultation with the authors (Appendix 1). This strategy will be peer reviewed by an Information Specialist using the Peer Review of Electronic Search Strategies (PRESS) Checklist (McGowan 2016a; McGowan 2016b). The MEDLINE strategy will be translated, using appropriate syntax, for other databases.

A population filter developed by Cochrane Neonatal will be used. The RCT search filter for Ovid MEDLINE, as recommended by Cochrane Neonatal, will be adapted to the syntax of PubMed (NLM) and used to identify randomized and quasi‐randomized studies. Searches for eligible trials will be conducted without language, publication year, publication type, or publication status restrictions.

Electronic searches

We will search the following databases:

  • Cochrane CENTRAL Register of Controlled Trials (CENTRAL), via Wiley;

  • PubMed (National Library of Medicine) (1946 to present); and

  • Embase.com, (Elsevier) (1974 to present).

Searching other resources

We will identify trial registration records using CENTRAL and by independent searches of:

We will screen the reference lists of included studies and related systematic reviews for studies not identified by the database searches.

We will search for errata or retractions for included studies published on PubMed (www.ncbi.nlm.nih.gov/pubmed).

Data collection and analysis

For each included study, we will collect information regarding the method of randomization, blinding, intervention, stratification, and whether the trial was single‐ or multicenter. We will note information regarding trial participants, including birth weight, gestational age, number of participants, indication for lumbar puncture and position of the infant for the lumbar puncture procedure. We will analyze the clinical outcomes noted above in Types of outcome measures.

Selection of studies

We will download all titles and abstracts retrieved by electronic searching to a reference management software and remove duplicates. If the number of search results is in excess of 1000, we will use Cochrane's Screen4Me to reduce screening activities by the authors. Screen4Me comprises three components:

  • known assessments (a service that matches records in the search results to records that have been screened by Cochrane Crowd and labeled as 'RCT' or 'not an RCT');

  • the RCT classifier (a machine‐learning model that distinguishes RCTs from non‐RCTs);

  • Cochrane Crowd (Cochrane’s crowd‐sourcing platform, where contributors from around the world help to identify randomized trials and other types of healthcare‐related research).

We will add any references rejected as non‐RCTs by Screen4Me to the 'Irrelevant' segment of Covidence, and save results in an RIS‐formatted text file suitable for import into bibliographic management or other software. This approach will mean references are available for the purposes of deduplication when the review is updated; and for verification purposes should questions arise about the accuracy of Screen4Me categorization. We will present the results of Screen4Me in an appendix of the review; and incorporate the disposition of references in the PRISMA flow diagram (Liberati 2009).

Two review authors (SP, OR) will independently screen the remaining title/abstracts. They will then assess the full text of references included after title/abstract review, working independently. At any point in the screening process, review authors will resolve disagreements by discussion or with a third review author (MB). We will document the reasons for excluding studies during review of full texts in a 'Characteristics of excluded studies' table; reasons for exclusion will be the absence of one or more PIC‐S (population, intervention, comparison, study design) elements; where a study omits more than one PIC‐S element, we will document only one. We will collate multiple reports of the same study so that each study, rather than each report, is the unit of interest in the review. We will also provide any information we can obtain about ongoing studies. We will record the selection process in sufficient detail to complete a PRISMA flow diagram (Liberati 2009).

Data extraction and management

Two review authors (SP, OR) will independently extract data using a data extraction form integrated with a modified version of the Cochrane Effective Practice and Organisation of Care Group data collection checklist (Cochrane EPOC Group 2017). We will pilot the form within the review team using a sample of included studies.

We will extract the following characteristics from each included study.

  • Administrative details: study author(s); published or unpublished; year of publication; year in which study was conducted; presence of vested interest; details of other relevant papers cited.

  • Study characteristics: study registration, study design type, study setting, number of study centers and location; informed consent; ethics approval, completeness of follow‐up (e.g. greater than 80%).

  • Participants: number randomized, number lost to follow‐up/withdrawn, number analyzed, mean (and range) gestational age, mean (and range)chronological age, sex, severity of condition, diagnostic criteria, inclusion criteria and exclusion criteria.

  • Interventions: characteristics of the position for the lumbar puncture.

  • Outcomes as mentioned above under Types of outcome measures.

We will resolve any disagreements by discussion.

We will describe ongoing studies identified by our search and document available information such as the primary author, research question(s), methods, and outcome measures, together with an estimate of the reporting date, and report them in the 'Characteristics of ongoing studies' table.

Should any queries arise, or in cases for which additional data are required, we will contact study investigators/authors for clarification. Two review authors (SP, OR) will use Cochrane statistical software for data entry (Review Manager 2020). We will replace any standard error of the mean (SEM) by the corresponding SD.

Assessment of risk of bias in included studies

Two review authors (SP, OR) will independently assess the risk of bias (low, high, or unclear) of all included trials using the Cochrane risk of bias tool for the following domains (Higgins 2017).

  • Random sequence generation (selection bias)

  • Allocation concealment (selection bias)

  • Blinding of participants and personnel (performance bias)

  • Blinding of outcome assessment (detection bias)

  • Incomplete outcome data (attrition bias)

  • Selective reporting (reporting bias)

  • Any other bias

We will resolve any disagreements by discussion or by consulting a third review author (MB). See Appendix 2 for a more detailed description of risk of bias for each domain. We will assess overall risk of bias according to three categories, as follows.

  • Low risk of bias: we will classify the outcome result of a trial as being at low risk of bias overall only if all domains were classified as being at low risk of bias.

  • Unclear risk of bias: we will classify the outcome result of a trial as being at unclear risk of bias overall if one or more domains were classified as being at unclear risk of bias, and no domain was at high risk of bias.

  • High risk of bias: we will classify the outcome result of a trial as being at high risk of bias overall if at least one domain was classified as being at high risk of bias.

Measures of treatment effect

Dichotomous data

For dichotomous data we will present results using risk ratios (RR) and risk differences (RD) with 95% confidence intervals (CIs). We will calculate the number needed to treat for an additional beneficial outcome (NNTB), or number needed to treat for an additional harmful outcome (NNTH) with 95% CIs if there is a statistically significant reduction (or increase) in RD.

Continuous data

For continuous data we will use the mean difference (MD) when outcomes were measured in the same way between trials. We will use the standardized mean difference (SMD) to combine trials that measured the same outcome but used different methods. Where trials reported continuous data as median and interquartile range (IQR) and data passed the test of skewness, we will convert mean to median and estimate the standard deviation as IQR/1.35.

If data are not reported by an RCT in a format that can be entered directly into a meta‐analysis, we will convert them to the required format using the information inChapter 6 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022a).

Unit of analysis issues

We will perform the primary analysis per individual randomized.

For cluster‐randomized trials, we will abstract information on the study design and unit of analysis for each study, indicating whether clustering of observations is present due to allocation to the intervention at the group level or clustering of individually randomized observations (e.g. patients within clinics). We will abstract available statistical information needed to account for the implications of clustering on the estimation of outcome variances, such as design effects or intracluster correlations, and whether the study adjusted results for the correlations in the data. In cases where the study does not account for clustering, we will ensure that we make appropriate adjustments to the effective sample size following Cochrane guidance (Higgins 2022b). Where possible, we will derive the intracluster correlation (ICC) for these adjustments from the trial itself, or from a similar trial. If an appropriate ICC is unavailable, we will conduct sensitivity analyses to investigate the potential effect of clustering by imputing a range of values of ICC.

If any trials have multiple arms that are compared against the same control condition that will be included in the same meta‐analysis, we will either combine groups to create a single pair‐wise comparison, or select one pair of interventions and exclude the others.

In the meta‐analysis and data synthesis, we will only include the first‐phase data from cross‐over trials.

Dealing with missing data

Where feasible, we intend to carry out analysis on an intention‐to‐treat basis for all outcomes. Whenever possible, we will analyze all participants in the treatment group to which they were randomized, regardless of the actual treatment received. If we identify important missing data (in the outcomes) or unclear data, we will request the missing data by contacting the original investigators. We will make explicit the assumptions of any methods used to deal with missing data. We may perform sensitivity analyses to assess how sensitive results are to reasonable changes in the assumptions made. We will address the potential impact of missing data on the findings of the review in the 'Discussion' section.

Assessment of heterogeneity

We will describe the clinical diversity and methodological variability of the evidence narratively and in tables. Tables will include data on study characteristics, such as design features, population characteristics, and intervention details.

To assess statistical heterogeneity, we will visually inspect forest plots and describe the direction and magnitude of effects and the degree of overlap between confidence intervals. We will also consider the statistics generated in forest plots that measure statistical heterogeneity. We will use the I2 statistic to quantify inconsistency among the trials in each analysis. We will also consider the P value from the Chi2 test to assess if this heterogeneity is significant (P < 0.1). If we identify substantial heterogeneity we will report the finding and explore possible explanatory factors using prespecified subgroup analysis.

We will grade the degree of heterogeneity as:

  • 0% to 40% might not represent important heterogeneity;

  • 30% to 60% may represent moderate heterogeneity;

  • 50% to 90% may represent substantial heterogeneity;

  • more than 75% may represent considerable heterogeneity.

We will use this as a rough guideline to interpret the I2 value rather than a simple threshold, and our interpretation will take into account an understanding that measures of heterogeneity (I2) will be estimated with high uncertainty when the number of studies is small (Deeks 2022).

Assessment of reporting biases

We will assess reporting bias by comparing the stated primary outcomes and secondary outcomes against the reported outcomes. Where study protocols are available, we will compare these to the full publications to determine the likelihood of reporting bias. Studies using the interventions in a potentially eligible infant population but not reporting on any of the primary and secondary outcomes will be documented in the 'Characteristics of included studies' tables.

We will use funnel plots to screen for publication bias where there are a sufficient number of studies (> 10) reporting the same outcome (Higgins 2022b). If publication bias is suggested by a significant asymmetry of the funnel plot on visual assessment, we will incorporate this in our assessment of certainty of evidence (Egger 1997). If our review includes few studies eligible for meta‐analysis the ability to detect publication bias will be largely diminished, and we will simply note our inability to rule out possible publication bias or smalls study effects.

Data synthesis

If we identify multiple studies that we consider to be sufficiently similar, we will perform meta‐analysis using Review Manager (Review Manager 2020). For categorical outcomes, we will calculate the typical estimates of RR and RD, each with its 95% CI; for continuous outcomes, we will calculate the MD or the SMD, each with its 95% CI. We will use a fixed‐effect model to combine data where it is reasonable to assume that studies were estimating the same underlying treatment effect. If we judge meta‐analysis to be inappropriate, we will analyze and interpret individual trials separately. If there is evidence of clinical heterogeneity, we will try to explain this based on the different study characteristics and subgroup analyses.

Subgroup analysis and investigation of heterogeneity

Tests for subgroup differences in effects will be interpreted with caution given the potential for confounding with other study characteristics and the observational nature of the comparisons. See Section 10.11.2 of Deeks 2022. In particular, subgroup analyses with fewer than five studies per category are unlikely to be adequate to ascertain valid difference in effects and will not be highlighted in our results. When subgroup comparisons are possible, we will conduct stratified meta‐analysis and a formal statistical test for interaction to examine subgroup differences that could account for effect heterogeneity (e.g. Cochran’s Q test, meta‐regression) (Borenstein 2013; Higgins 2022b).

Given the potential differences in the intervention effectiveness related to gestational age and birthweight discussed in the Background section, we will conduct subgroup comparisons of these characteristics to see if the intervention is more effective for the management of pain and discomfort during lumbar puncture in newborn infants.

We plan to carry out the following subgroup analyses of factors that may contribute to heterogeneity in the effects of the intervention.

  • Prematurity: term; preterm

  • Body weight: less than 1500 g; 1500 to 2500 g; more than 2500 g

  • With or without intraventricular hemorrhage

  • Timing of stylet removal: early; late

  • Size and length of lumbar puncture needle

  • Experience of the operator performing the lumbar puncture

We will use the main outcomes in subgroup analyses if there are enough studies reporting to support valid subgroup comparisons (at least five studies per subgroup).

Sensitivity analysis

If we identify substantial heterogeneity, we will conduct sensitivity analysis to determine if the findings are affected by the inclusion of only those trials considered to have used adequate methodology with a low risk of bias (selection, performance and reporting bias). We will report the results of sensitivity analyses for primary outcomes only.

Given that there is no formal statistical test that can be used for sensitivity analysis, we will provide informal comparisons between the different ways of estimating the effect under different assumptions. Changes in the P values should not be used to judge whether there is a difference between the main analysis and sensitivity analysis, since statistical significance may be lost with fewer studies included.

We will report sensitivity analysis results in tables rather than forest plots.

Summary of findings and assessment of the certainty of the evidence

We will use the GRADE approach, as outlined in the GRADE Handbook (Schünemann 2013; Schünemann 2022), to assess the certainty of evidence for the following (clinically relevant) outcomes.

  • Successful lumbar puncture procedure at the first attempt, with < 1 × 109 red blood cells/L

  • Total number of lumbar puncture attempts

  • Episodes of bradycardia, defined as a fall in heart rate of more than 30% below the baseline or less than 100 beats per minute for 10 seconds or longer

  • Time to perform the lumbar puncture

  • Episodes of desaturation, defined as a decrease of arterial oxygen saturation (SpO2) to less than 80%, with no minimum duration specified

  • Apnea: number of episodes (defined as interruption of breathing for more than 20 seconds) during the procedure

  • Apnea: number of infants with one or more episodes (defined as interruption of breathing for more than 20 seconds) during the procedure

Two review authors (SP, MB) will independently assess the certainty of the evidence for each of the outcomes above. We will include a summary of findings table for each of the specified comparison in Types of interventions. We will consider evidence from RCTs as high certainty, downgrading the evidence one level for serious (or two levels for very serious) limitations based upon the following: design (risk of bias), consistency across studies, directness of the evidence, precision of estimates, and presence of publication bias. We will use the GRADEpro GDT Guideline Development Tool to create a summary of findings table to report the certainty of the evidence.

The GRADE approach results in an assessment of the certainty of a body of evidence in one of the following four grades.

  • High: we are very confident that the true effect lies close to that of the estimate of the effect.

  • Moderate: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.

  • Low: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect.

  • Very low: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate of effect.