Pyridoxal 5 phosphate for neuroleptic‐induced tardive dyskinesia (Protocol)

Pyridoxal 5 phosphate for neuroleptic-induced tardive

dyskinesia (Protocol)

Adelufosi AO, Abayomi O, Ojo TMF

This is a reprint of a Cochrane protocol, prepared and maintained by The Cochrane Collaboration and published in The Cochrane

Library 2013, Issue 4

http://www.thecochranelibrary.com

Pyridoxal 5 phosphate for neuroleptic-induced tardive dyskinesia (Protocol)

Copyright © 2013 The Cochrane Collaboration. Published by John Wiley & Sons, Ltd.

http://www.thecochranelibrary.com

T A B L E O F C O N T E N T S

1HEADER . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

1ABSTRACT . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

1BACKGROUND . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

2OBJECTIVES . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

2METHODS . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

8ACKNOWLEDGEMENTS . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

9REFERENCES . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

11CONTRIBUTIONS OF AUTHORS . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

11DECLARATIONS OF INTEREST . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

11SOURCES OF SUPPORT . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

iPyridoxal 5 phosphate for neuroleptic-induced tardive dyskinesia (Protocol)


[Intervention Protocol]

Pyridoxal 5 phosphate for neuroleptic-induced tardivedyskinesia

Adegoke Oloruntoba Adelufosi1, Olukayode Abayomi2, Tunde Massey-Ferguson Ojo3

1Department of Psychiatry, LAUTECH Teaching Hospital, Ogbomoso, Nigeria. 2Psychiatry, Ladoke Akintola University Teaching

Hospital, Ogbomoso, Nigeria. 3Clinicial Sciences (Resident Doctors Office), Neuropsychiatric Hospital, Ogun State, Nigeria

Contact address: Adegoke Oloruntoba Adelufosi, Department of Psychiatry, LAUTECH Teaching Hospital, Ogbomoso, Oyo State,

Nigeria. [email protected].

Editorial group: Cochrane Schizophrenia Group.

Publication status and date: New, published in Issue 4, 2013.

Citation: Adelufosi AO, Abayomi O, Ojo TMF. Pyridoxal 5 phosphate for neuroleptic-induced tardive dyskinesia. Cochrane Database

of Systematic Reviews 2013, Issue 4. Art. No.: CD010501. DOI: 10.1002/14651858.CD010501.


A B S T R A C T

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

To determine the effects of pyridoxal 5 phosphate (pyridoxine, pyridoxal phosphate, tardoxal) for treating neuroleptic-induced tardive

dyskinesia in individuals of any age group with schizophrenia and other psychotic disorders.

B A C K G R O U N D

Description of the condition

Since 1950 when the first antipsychotic medication was dis-

covered, the symptoms of schizophrenia and other related psy-

chotic disorders, especially hallucinations and delusions, have been

treated effectively with neuroleptic medications; these, however

can have distressing side-effects such as tardive dyskinesia.

Tardive dyskinesia is a late onset, movement disorder often re-

sulting from long-term use of neuroleptic (antipsychotic) medica-

tions. It manifests as repetitive, involuntary movements affecting

the face, jaw, tongue, extremities and the trunk. Abnormal move-

ments in tardive dyskinesia may involve tongue darting, repeti-

tive grimacing, chewing movements of the mouth, sucking move-

ments or puckering of the lips and purposeless, irregular, jerking

movements of the limbs. These symptoms are highly stigmatis-

ing and associated with poor quality of life in affected individuals

(Browne 1996).

Risk factors for tardive dyskinesia in patients with schizophre-

nia include female gender (Yassa 1992), older age (Niehaus

2008; Smith 1980), cognitive impairment or neurological deficits

(Waddington 1987), diagnosis of a mood disorder especially de-

pression (Casey 1995; Sachdev 1989; Kane 1986), worsening of

psychopathology (Tenback 2007) and diabetes mellitus (Casey

1995; Woerner 1993). Tardive dyskinesia is also higher among

those taking first generation (conventional) antipsychotic drugs

compared with those on second generation (atypical) antipsychotic

medications (Corell 2008; Nasrallah 2006). However, neuroleptic

medications are not the sole cause of tardive dyskinesia, as similar

abnormal motor movements has been reported among patients

with schizophrenia who were never exposed to neuroleptic medi-

cations (Fenton 2000; Owens 1982).

The exact pathogenesis of tardive dyskinesia is unknown and sev-

1Pyridoxal 5 phosphate for neuroleptic-induced tardive dyskinesia (Protocol)


mailto:[email protected]

eral theories about its aetiology has been proposed. Foremost is the

dopamine receptor supersensitivity hypothesis which posits that

long-term receptor antagonism by antipsychotic drugs results in

dopamine receptor supersensitivity and the movement disorder in

tardive dyskinesia (Sachdev 1989). The neurotoxicity hypothesis

states that tardive dyskinesia results from the neurotoxic effects

of free radicals that are released during dopamine metabolism. It

is believed that these free radicals cause cellular degeneration of

striatal GABA-ergic neurons, leading to the loss of their inhibitory

activities and the hyperkinetic state of tardive dyskinesia (Sachdev

1989). The use of antioxidants such as vitamin B6 (pyridoxine)

as possible treatment for tardive dyskinesia symptoms is based on

the neurotoxicity hypothesis (Lerner 2007).

There are reports that pyridoxal 5 phosphate, a metabolite of

vitamin B6 (pyridoxine) helps in alleviating these symptoms

(Miodownik 2008; Lerner 2007).

Description of the intervention

Pyridoxal 5 phosphate is the metabolically active form of vitamin

B6 (pyridoxine). Vitamin B6 is a naturally occurring vitamin that

can be obtained from both animal and plant sources. Following

ingestion, pyridoxine is absorbed from the upper small intestine,

where it is transported to the liver and oxidised to form pyridoxal.

It is then phosphorylated by pyridoxal kinase to form pyridoxal 5

phosphate. Unlike pyridoxine, which causes peripheral neuropa-

thy when high doses are given, pyridoxal 5 phosphate is not as-

sociated with any known adverse effects even at doses as high as

1200 mg/day (Miodownik 2008; Schaumburg 1983).

How the intervention might work

Pyridoxal 5 phosphate is a coenzyme in the decarboxylation of

DOPA leading to the production of neurotransmitters such as

serotonin, dopamine, gamma amino butyric acid (GABA). Al-

though its actual mechanism of action is not clear, it is believed

that the role of pyridoxal 5 phosphate in the synthesis of these

neurotransmitters accounts for its ability to reduce the symptoms

of tardive dyskinesia (Lerner 2001). Thus, by promoting neuro-

transmitter synthesis, pyridoxine may reduce the symptoms of tar-

dive dyskinesia (Lerner 2001).

Why it is important to do this review

Tardive dyskinesia is very disabling and disfiguring and its occur-

rence is associated with poor treatment adherence (Barnes 1993)

and low quality of life (Browne 1996). The reported prevalence

of tardive dyskinesia ranged from 3% to 70% with a median of

24% among patients on long-term use of neuroleptic medications

(Yassa 1992).The annual incidence is 5.2% in those with a first

episode schizophrenia placed on neuroleptic medications, the rate

increasing to about 20% at five years (Chakos 1996). Several drugs

have been used in an attempt to treat tardive dyskinesia, but little

evidence exists to support their efficacy. Such interventions include

melatonin (Nelson 2003), cholinergic agonists (Caroff 2001), vi-

tamin E (Adler 1998), calcium channel blockers (Fay-McCarthy

1997) and clozapine (Bassitt 1998). While the evidence for the

effectiveness for some of these interventions has been evaluated

(McGrath 2001; Soares-Weiser 2004; Tammenmaa 2002), no

evaluation has taken place for pyridoxal 5 phosphate. Thus, it is

uncertain if pyridoxal 5 phosphate is effective in the treatment

of neuroleptic-induced tardive dyskinesia. This review may pro-

vide evidence for its efficacy in the treatment of tardive dyskinesia

among patients with schizophrenia and other psychotic disorders.

O B J E C T I V E S

To determine the effects of pyridoxal 5 phosphate (pyridoxine,

pyridoxal phosphate, tardoxal) for treating neuroleptic-induced

tardive dyskinesia in individuals of any age group with schizophre-

nia and other psychotic disorders.

M E T H O D S

Criteria for considering studies for this review

Types of studies

All relevant randomised controlled trials. If a trial is described as

’double blind’ but implies randomisation, we will include such tri-

als in a sensitivity analysis (see Sensitivity analysis). If their inclu-

sion does not result in a substantive difference, they will remain in

the analyses. If their inclusion does result in important clinically

significant, but not necessarily statistically significant differences,

we will not add the data from these lower quality studies to the

results of the better trials, but will present such data within a sub-

category. We will exclude quasi-randomised studies, such as those

allocating by alternate days of the week. Where people are given

additional treatments to pyridoxal 5 phosphate, we will only in-

clude the data if the adjunct treatment is evenly distributed be-

tween groups and it is only pyridoxal 5 phosphate that is ran-

domised.

Types of participants

People with schizophrenia or other chronic mental illness, diag-

nosed by any criteria, irrespective of gender, age or nationality,

who:



1. require the use of antipsychotics for more than three

months;

2. develope tardive dyskinesia (diagnosed by any criteria at

baseline and at least one other occasion) during antipsychotic

treatment; and

3. for whom the dose of antipsychotic medication has been

stable for one month or more (the same applies for those free of

antipsychotics).

We will only include trials where the majority of participants have

a diagnosis of schizophrenia.

Types of interventions

1. Pyridoxal 5 phosphate (pyridoxal phosphate, pyridoxine,

vitamin B6): any dose or means of administration.

2. Placebo or no intervention.

Types of outcome measures

We will group the outcomes by duration of treatment into short

term (less than six weeks), medium term (between six weeks and

six months) and long term (over six months).

Primary outcomes

1. Global state: Clinical efficacy will be defined as an

improvement in the symptoms of tardive dyskinesia of more

than 50%, on any peer-reviewed scale, after at least six weeks

of intervention

Secondary outcomes

1. Global Outcomes

1.1 Death due to suicide or other causes

1.2 Average endpoint dose of pyridoxal 5 phosphate or

vitamin B6

1.3 Any adverse effects (other than deterioration of tardive

dyskinesia symptoms or change in mental state)

1.4 Average time to discontinuation of pyridoxal 5 phosphate and

reasons for discontinuation

2. Tardive dyskinesia

2.1 Deterioration in tardive dyskinesia symptoms

2.2 Average endpoint tardive dyskinesia score

3. General mental state changes

3.1 Any deterioration in psychiatric symptoms (such as

delusions and hallucinations)

3.2 Average endpoint psychiatric symptoms score

4. Summary of findings table

We will use the GRADE approach to interpret findings (

Schünemann 2008) and will use GRADE profiler (GRADEPRO)

to import data from RevMan 5 (Review Manager) to create ’Sum-

mary of findings’ tables. These tables provide outcome-specific

information concerning the overall quality of evidence from each

included study in the comparison, the magnitude of effect of the

interventions examined, and the sum of available data on all out-

comes we rate as important to patient-care and decision-making.

We aim to select all of our listed outcomes for inclusion in the

’Summary of findings’ table.

Search methods for identification of studies

No language restriction will be applied within the limitations of

the search tools.

Electronic searches

1. Cochrane Schizophrenia Group Trials Register

The Trials Search Co-ordinator will search the Cochrane

Schizophrenia Group’s Trials Register using the phrase:

[*Pyridoxal* OR *Pyridoxine* OR *P5P* OR *PLP* OR *tar-

doxal* OR *Vitamin B6* O *Vitamin B 6* R in title, abstract or

index terms of REFERENCE, or interventions of STUDY]

The Cochrane Schizophrenia Group’s Trials Register is compiled

by systematic searches of major databases, handsearches of journals

and conference proceedings (see Group Module). Incoming trials

are assigned to relevant existing or new review titles.



http://www.ims.cochrane.org/revman/gradepro

http://www.ims.cochrane.org/revman

http://www.ims.cochrane.org/revman

http://onlinelibrary.wiley.com/o/cochrane/clabout/articles/SCHIZ/frame.html

http://onlinelibrary.wiley.com/o/cochrane/clabout/articles/SCHIZ/frame.html

Searching other resources

1. Reference searching

We will inspect references of all identified studies for more studies.

2. Personal communication

We will contact the first author of each included study for more

information regarding unpublished trials.

3. Pharmaceutical companies

We will contact Medicure Pharmaceutical company for informa-

tion on unpublished or ongoing studies.

Data collection and analysis

Selection of studies

Review authors AOA and OA will independently inspect citations

from the searches and identify relevant abstracts. A random 20%

sample will be independently re-inspected by TMO to ensure

reliability. Where disputes arise, the full report will be acquired for

more detailed scrutiny. Full reports of the abstracts meeting the

review criteria will be obtained and inspected by AOA and OA.

Again, a random 20% of reports will be re-inspected by TMO

in order to ensure reliable selection. Where it is not possible to

resolve disagreement by discussion, we will attempt to contact the

authors of the study for clarification.

Data extraction and management

1. Extraction

Review authors AOA and OA will extract data from all included

studies. In addition, to ensure reliability, TMO will independently

extract data from a random sample of these studies, comprising

10% of the total. Again, any disagreement will be discussed, de-

cisions documented and, if necessary, we will contact the authors

of studies for clarification. With remaining problems, TMO will

help clarify issues and these final decisions will be documented.

Data presented only in graphs and figures will be extracted when-

ever possible, but will only be included if two review authors in-

dependently have the same result. We will attempt to contact au-

thors through an open-ended request in order to obtain missing

information or for clarification whenever necessary. If studies are

multicentre, where possible, we will extract data relevant to each

component centre separately.

2. Management

2.1 Forms

We will extract data onto standard, simple forms.

2.2 Scale-derived data

We will include continuous data from rating scales only if:

a) the psychometric properties of the measuring instrument have

been described in a peer-reviewed journal (Marshall 2000); and

b) the measuring instrument has not been written or modified by

one of the trialists for that particular trial.

Ideally the measuring instrument should either be i. a self-report

or ii. completed by an independent rater or relative (not the thera-

pist). We realise that this is not often reported clearly, in ’Descrip-

tion of studies’ we will note if this is the case or not.

2.3 Endpoint versus change data

There are advantages of both endpoint and change data. Change

data can remove a component of between-person variability from

the analysis. On the other hand, calculation of change needs two

assessments (baseline and endpoint) which can be difficult in un-

stable and difficult to measure conditions such as schizophrenia.

We have decided primarily to use endpoint data, and only use

change data if the former are not available. Endpoint and change

data will be combined in the analysis as we will use mean dif-

ferences (MD) rather than standardised mean differences (SMD)

throughout (Higgins 2011 ).

2.4 Skewed data

Continuous data on clinical and social outcomes are often not

normally distributed. To avoid the pitfall of applying parametric

tests to non-parametric data, we aimed to apply the following

standards to all data before inclusion:

a) standard deviations (SDs) and means are reported in the paper

or obtainable from the authors;

b) when a scale starts from the finite number zero, the SD, when

multiplied by two, is less than the mean (as otherwise the mean is

unlikely to be an appropriate measure of the centre of the distri-

bution, (Altman 1996);

c) if a scale started from a positive value (such as the Positive and

Negative Syndrome Scale (PANSS), (Kay 1986)), which can have

values from 30 to 210), the calculation described above will be

modified to take the scale starting point into account. In these

cases skew is present if 2 SD > (S-S min), where S is the mean

score and ’S min’ is the minimum score.

Endpoint scores on scales often have a finite start and end point

and these rules can be applied. Skewed data pose less of a problem



when looking at means if the sample size is large (> 200) and

we will enter these into the syntheses. We will present skewed

endpoint data from studies of less than 200 participants as other

data within the data and analyses section rather than enter such

data into statistical analyses.

When continuous data are presented on a scale that includes a

possibility of negative values (such as change data), it is difficult

to tell whether data are skewed or not. We will present and enter

all useable change data into analyses.

2.5 Common measure

To facilitate comparison between trials, we intend to convert vari-

ables that can be reported in different metrics, such as days in hos-

pital (mean days per year, per week or per month) to a common

metric (e.g. mean days per month).

2.6 Conversion of continuous to binary

Where possible, efforts will be made to convert outcome measures

to dichotomous data. This can be done by identifying cut-off

points on rating scales and dividing participants accordingly into

’clinically improved’ or ’not clinically improved’. It is generally

assumed that if there is a 50% reduction in a scale-derived score

such as the Brief Psychiatric Rating Scale (BPRS, Overall 1962)

or the PANSS(Kay 1986), this could be considered as a clinically

significant response (Leucht 2005; Leucht 2005a). If data based

on these thresholds are not available, we will use the primary cut-

off presented by the original authors.

2.7 Direction of graphs

Where possible, we will enter data in such a way that the area to

the left of the line of no effect indicates a favourable outcome for

pyridoxal 5 phosphate. Where keeping to this makes it impossible

to avoid outcome titles with clumsy double-negatives (e.g. ’Not

improved’) we will report data where the left of the line indicates an

unfavourable outcome. This will be noted in the relevant graphs.

Assessment of risk of bias in included studies

Again review authors AOA and OA will work independently to

assess risk of bias by using criteria described in the Cochrane Hand-

book for Systemic reviews of Interventions (Higgins 2011) to assess

trial quality. This set of criteria is based on evidence of associations

between overestimate of effect and high risk of bias of the article

such as sequence generation, allocation concealment, blinding, in-

complete outcome data and selective reporting.

If the raters disagree, the final rating will be made by consensus,

with the involvement of another member of the review group.

Where inadequate details of randomisation and other characteris-

tics of trials are provided, we will contact the authors of the studies

in order to obtain further information. Non-concurrence in qual-

ity assessment will be reported, but if disputes arise as to which

category a trial is to be allocated, again, we will resolve by discus-

sion.

The level of risk of bias will be noted in both the text of the review

and in the ’Summary of findings’ table.

Measures of treatment effect

1. Binary data

For binary outcomes, we will calculate a standard estimation of

the risk ratio (RR) and its 95% confidence interval (CI). It has

been shown that RR is more intuitive (Boissel 1999) than odds

ratios and that odds ratios tend to be interpreted as RR by clin-

icians (Deeks 2000). The number needed to treat/harm (NNT/

H) statistic with its confidence intervals is intuitively attractive

to clinicians but is problematic both in its accurate calculation in

meta-analyses and interpretation (Hutton 2009). For binary data

presented in the ’Summary of findings’ tables, where possible, we

aim to calculate illustrative comparative risks.

2. Continuous data

For continuous outcomes, we will estimate the MD between

groups. We would prefer not to calculate effect size measures

(SMD). However, if scales of very considerable similarity were

used, we will presume there is a small difference in measurement,

and we will calculate effect size and transform the effect back to

the units of one or more of the specific instruments.

Unit of analysis issues

1. Cluster trials

Studies increasingly employ ’cluster randomisation’ (such as ran-

domisation by clinician or practice) but analysis and pooling of

clustered data poses problems. Firstly, authors often fail to account

for intra-class correlation in clustered studies, leading to a ’unit

of analysis’ error (Divine 1992), whereby P values are spuriously

low, confidence intervals unduly narrow and statistical significance

overestimated. This causes type I errors (Bland 1997; Gulliford

1999).

Where clustering is not accounted for in primary studies, we will

present data in a table, with a (*) symbol to indicate the presence

of a probable unit of analysis error. In subsequent versions of this

review, we will seek to contact the first authors of studies to ob-

tain intra-class correlation coefficients (ICCs) for their clustered

data and to adjust for this by using accepted methods (Gulliford

1999). Where clustering has been incorporated into the analysis



of primary studies, we will present these data as if from a non-

cluster randomised study, but adjust for the clustering effect.

We have sought statistical advice and have been advised that the

binary data as presented in a report should be divided by a ’design

effect’. This is calculated using the mean number of participants

per cluster (m) and the ICC [Design effect = 1+(m-1)*ICC] (

Donner 2002). If the ICC is not reported, it will be assumed to

be 0.1 (Ukoumunne 1999).

If cluster studies have been appropriately analysed taking into ac-

count ICCs and relevant data documented in the report, synthesis

with other studies will be possible using the generic inverse vari-

ance technique.

2. Cross-over trials

A major concern of cross-over trials is the carry-over effect. It oc-

curs if an effect (e.g. pharmacological, physiological or psycho-

logical) of the treatment in the first phase is carried over to the

second phase. As a consequence, on entry to the second phase

the participants can differ systematically from their initial state

despite a wash-out phase. For the same reason cross-over trials are

not appropriate if the condition of interest is unstable (Elbourne

2002). As both effects are very likely in severe mental illness, we

will only use data of the first phase of cross-over studies.

3. Studies with multiple treatment groups

Where a study involves more than two treatment arms, if rele-

vant, the additional treatment arms will be presented in compar-

isons. If data are binary, these will be simply added and combined

within the two-by-two table. If data are continuous, we will com-

bine data following the formula in section 7.7.3.8 (Combining

groups) of the Cochrane Handbook for Systemic reviews of Interven-

tions (Higgins 2011). Where the additional treatment arms are not

relevant, we will not use these data.

Dealing with missing data

1. Overall loss of credibility

At some degree of loss of follow-up, data must lose credibility (Xia

2009). We choose that, for any particular outcome, should more

than 50% of data be unaccounted for, we will not reproduce these

data or use them within analyses. If, however, more than 50% of

those in one arm of a study are lost, but the total loss is less than

50%, we will address this within the ’Summary of findings’ tables

by down-rating quality. Finally, we will also downgrade quality

within the ’Summary of findings’ tables should loss be 25% to

50% in total.

2. Binary

In the case where attrition for a binary outcome is between 0% and

50% and where these data are not clearly described, we will present

data on a ’once-randomised-always-analyse’ basis (an intention-

to-treat analysis). Those leaving the study early are all assumed to

have the same rates of negative outcome as those who completed,

with the exception of the outcome of death and adverse effects.

For these outcomes, the rate of those who stay in the study - in

that particular arm of the trial - will be used for those who did

not. We will undertake a sensitivity analysis to test how prone the

primary outcomes are to change when data only from people who

complete the study to that point are compared with the intention-

to-treat analysis using the above assumptions.

3. Continuous

3.1 Attrition

In the case where attrition for a continuous outcome is between

0% and 50%, and data only from people who complete the study

to that point are reported, we will reproduce these.

3.2 Standard deviations

If standard deviations (SDs) are not reported, we will first try to

obtain the missing values from the authors. If not available, where

there are missing measures of variance for continuous data, but

an exact standard error (SE) and confidence intervals are available

for group means, and either a ’P’ value or ’t’ value available for

differences in mean, we can calculate them according to the rules

described in the Cochrane Handbook for Systemic reviews of Inter-

ventions (Higgins 2011): When only the SE is reported, SDs are

calculated by the formula SD = SE * square root (n). Chapters

7.7.3 and 16.1.3 of the Cochrane Handbook for Systemic reviews of

Interventions (Higgins 2011) present detailed formulae for estimat-

ing SDs from P values, t or F values, confidence intervals, ranges

or other statistics. If these formulae do not apply, we will calcu-

late the SDs according to a validated imputation method which is

based on the SDs of the other included studies (Furukawa 2006).

Although some of these imputation strategies can introduce error,

the alternative would be to exclude a given study’s outcome and

thus to lose information. We nevertheless will examine the valid-

ity of the imputations in a sensitivity analysis excluding imputed

values.

3.3 Last observation carried forward

We anticipate that in some studies the method of last observation

carried forward (LOCF) will be employed within the study report.

As with all methods of imputation to deal with missing data,

LOCF introduces uncertainty about the reliability of the results



(Leucht 2007). Therefore, where LOCF data have been used in

the trial, if less than 50% of the data have been assumed, we will

present and use these data and indicate that they are the product

of LOCF assumptions.

Assessment of heterogeneity

1. Clinical heterogeneity

We will consider all included studies initially, without seeing com-

parison data, to judge clinical heterogeneity. We will simply in-

spect all studies for clearly outlying people or situations which we

had not predicted would arise. When such situations or partici-

pant groups arise, these will be fully discussed.

2. Methodological heterogeneity

We will consider all included studies initially, without seeing com-

parison data, to judge methodological heterogeneity. We will sim-

ply inspect all studies for clearly outlying methods which we had

not predicted would arise. When such methodological outliers

arise these will be fully discussed.

3. Statistical heterogeneity

3.1 Visual inspection

We will visually inspect graphs to investigate the possibility of

statistical heterogeneity.

3.2 Employing the I2 statistic

Heterogeneity between studies will be investigated by considering

the I2 method alongside the Chi2 ’P’ value. The I2 provides an

estimate of the percentage of inconsistency thought to be due to

chance (Higgins 2003). The importance of the observed value of I2 depends on i. magnitude and direction of effects and ii. strength

of evidence for heterogeneity (e.g. ’P’ value from Chi2 test, or a

confidence interval for I2). An I2 estimate greater than or equal to

around 50% accompanied by a statistically significant Chi2 statis-

tic, will be interpreted as evidence of substantial levels of hetero-

geneity (Section 9.5.2 - Higgins 2011). When substantial levels of

heterogeneity are found in the primary outcome, we will explore

reasons for heterogeneity (Subgroup analysis and investigation of

heterogeneity).

Assessment of reporting biases

1. Protocol versus full study

Reporting biases arise when the dissemination of research find-

ings is influenced by the nature and direction of results. These

are described in section 10.1 of the Cochrane Handbook for Sys-

temic reviews of Interventions (Higgins 2011). We will try to locate

protocols of included randomised trials. If the protocol is avail-

able, outcomes in the protocol and in the published report will be

compared. If the protocol is not available, outcomes listed in the

methods section of the trial report will be compared with actually

reported results.

2. Funnel plot

Reporting biases arise when the dissemination of research findings

is influenced by the nature and direction of results (Egger 1997).

These are again described in Section 10 of the Cochrane Handbook

for Systemic reviews of Interventions (Higgins 2011). We are aware

that funnel plots may be useful in investigating reporting biases

but are of limited power to detect small-study effects. We will

not use funnel plots for outcomes where there are 10 or fewer

studies, or where all studies are of similar sizes. In other cases,

where funnel plots are possible, we will seek statistical advice in

their interpretation.

Data synthesis

We understand that there is no closed argument for preference for

use of fixed-effect or random-effects models. The random-effects

method incorporates an assumption that the different studies are

estimating different, yet related, intervention effects. This often

seems to be true to us and the random-effects model takes into

account differences between studies even if there is no statistically

significant heterogeneity. There is, however, a disadvantage to the

random-effects model. It puts added weight onto small studies

which often are the most biased ones. Depending on the direction

of effect, these studies can either inflate or deflate the effect size.

We choose the random-effects model for all analyses. The reader

is, however, able to choose to inspect the data using fixed-effect

model.

Subgroup analysis and investigation of heterogeneity

1. Subgroup analyses

1.1 Primary outcomes

We do not anticipate any subgroup analyses.



1.2 Clinical state, stage or problem

We propose to undertake this review and provide an overview of

the effects of pyridoxal 5 phosphate for people with neuroleptic-

induced tardive dyskinesia in general. In addition, however, we

will try to report data on subgroups of people in the same clinical

state, stage and with similar problems.

2. Investigation of heterogeneity

If inconsistency is high, this will be reported. First, we will inves-

tigate whether data has been entered correctly. Second, if data are

correct, the graph will be visually inspected and outlying studies

will be removed to see if homogeneity is restored. For this review,

we have decided that should this occur with data contributing to

the summary finding of no more than around 10% of the total

weighting, data will be presented. If not, data will not be pooled

and issues will be discussed. We know of no supporting research

for this 10% cut-off but are investigating use of prediction inter-

vals as an alternative to this unsatisfactory state.

When unanticipated clinical or methodological heterogeneity are

obvious, we will simply state hypotheses regarding these for future

reviews or versions of this review. We do not anticipate undertaking

analyses relating to these.

Sensitivity analysis

1. Implication of randomisation

We aim to include trials in a sensitivity analysis if they are described

in some way as to imply randomisation. For the primary outcomes,

we will include these studies and if there is no substantive difference

when the implied randomised studies are added to those with

better description of randomisation, then all data will be employed

from these studies.

2. Assumptions for lost binary data

Where assumptions have to be made regarding people lost to fol-

low-up (see Dealing with missing data), we will compare the find-

ings of the primary outcomes when we use our assumption/s and

when we use data only from people who complete the study to

that point. If there is a substantial difference, we will report results

and discuss them but will continue to employ our assumption.

Where assumptions have to be made regarding missing SDs data

(see Dealing with missing data), we will compare the findings of

the primary outcomes when we use our assumption/s and when

we use data only from people who complete the study to that

point. A sensitivity analysis will be undertaken to test how prone

results are to change when completer-only data only are compared

with the imputed data using the above assumption. If there is a

substantial difference, we will report results and discuss them but

will continue to employ our assumption.

3. Risk of bias

We will analyse the effects of excluding trials that are judged to be

at high risk of bias across one or more of the domains of randomi-

sation (implied as randomised with no further details available)

allocation concealment, blinding and outcome reporting for the

meta-analysis of the primary outcome. If the exclusion of trials at

high risk of bias does not substantially alter the direction of effect

or the precision of the effect estimates, then data from these trials

will be included in the analysis.

4. Imputed values

We will also undertake a sensitivity analysis to assess the effects of

including data from trials where we used imputed values for ICC

in calculating the design effect in cluster randomised trials.

If substantial differences are noted in the direction or precision of

effect estimates in any of the sensitivity analyses listed above, we

will not pool data from the excluded trials with the other trials

contributing to the outcome, but will present them separately.

5. Fixed and random effects

All data will be synthesised using a random-effects model, however,

we will also synthesise data for the primary outcome using a fixed-

effect model to evaluate whether this alters the significance of the

results.

A C K N O W L E D G E M E N T S

The Cochrane Schizophrenia Group Editorial Base in Notting-

ham produces and maintains standard text for use in the Methods

sections of their reviews. This text has been used as the basis of

this protocol, with modifications where necessary.

Adegoke Oloruntoba Adelufosi was awarded a Reviews for Africa

(Nigeria) Programme Fellowship funded by a grant from the UK

Department for International Development (DFID) through the

Effective Healthcare Research Consortium at the Liverpool School

of tropical Medicine. This protocol was developed in part during

the Reviews for Africa Programme protocol development course

organised by the Nigerian Branch of South African Cochrane Cen-

tre, July 2012.

The search term was developed by the Trials Search Co-ordinator

of the Cochrane Schizophrenia Group, Samantha Roberts.

We acknowledge and thank Dr Ranganath D Rattehalli for peer-

reviewing this protocol and his helpful comments, and would also

like to thank Heather Maxwell from Cochrane Copy Edit Support

team for copy editing this protocol.



R E F E R E N C E S

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C O N T R I B U T I O N S O F A U T H O R S

Adegoke Oloruntoba Adelufosi - Developed the protocol.

Olukayode Abayomi - Assisted in writing the protocol.

Tunde Massey-Ferguson Ojo - Assisted in writing the protocol.

D E C L A R A T I O N S O F I N T E R E S T

The authors received no financial consideration from any parties for the preparation of this review.

S O U R C E S O F S U P P O R T

Internal sources

• Reviews for Africa (Nigeria) Programme Fellowship, Nigeria.

External sources

• UK Department for International Development (DFID) through the Effective Healthcare Research Consortium at the

Liverpool School of tropical Medicine., UK.



Pyridoxal 5 phosphate for neuroleptic‐induced tardive dyskinesia (Protocol)

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