The scientific validity of current approaches to
violence and criminal risk assessment
– submitted version
Criminal justice systems in many high-income countries use some form of structured
risk assessment tool or instrument to inform decisions about sentencing, parole,
release and probation . These tools typically consider two aspects – the future risk of
an individual for reoffending, and also the criminogenic needs to mitigate this future
risk. One estimate is that there are more than 300 such risk assessment tools (Singh,
Desmarais et al. 2014), many of which are heavily marketed and sold commercially.
In the US alone, one report based on a review from 1970 to 2012 documented that 39
states have their own risk assessment tools (Desmarais, Johnson et al. 2016). In
contrast, in England and Wales, there is one risk tool in place for prisons and
probation, called OASyS (Offender Assessment System), which has been revised as
its first edition was found to have poor predictive performance (Howard and Dixon
2012). Typically, such tools include a set of risk factors, which may or may not be
weighted, to provide a classification of risk (such as high, medium or low), or a
probabilistic score (i.e. a percentage probability of reoffending within a certain time-
frame), or both. At its most basic, a small number of static (or unchangeable) risk
factors, such as sex, age, and previous offending, are used to determine high, medium
or low risk but without any information as to what these categories actually mean in
terms of probabilities, data on accuracy, or how these risk factors translate into one of
these categories. The increasing use of these tools has been driven by the need to
provide more consistent and defensible estimates of future risk and, in tools that are
more focused on needs, better matching of treatment and interventions in criminal
justice with their limited resources. The needs-based approaches attempt to assess
individual factors that are thought to be related to offending, such as certain attitudes,
stable accommodation, relationship problems, and family support. The uptake of these
tools can also be explained by research findings, which suggest in general terms, that
they are better at prediction than human beings (Ægisdóttir, White et al. 2006), and
that unstructured clinical judgement (or the subjective judgement of individuals
without any explicit framework of assessment) may be biased for many different
reasons, including recent experience, prejudice against minority groups, and attitudes
towards certain offences.
This chapter will present a brief overview of performance measures for risk
assessment instruments, and then summarise a number of recent systematic reviews
examining the accuracy of commonly used instruments. I will then identify some gaps
in the field, and discuss whether the current tools are fit for purpose.
Measuring the statistical performance of risk assessment
There are two approaches to test to the performance of such instruments:
discrimination and calibration. Discrimination measures a particular tool’s ability to
distinguish between those who have offended and those who have not by assigning a
higher risk score or category to those who offend. Discrimination is tested by
reporting sensitivity, specificity, positive predictive value and negative predictive
value (see definitions below), which can only be calculated at specific risk cut-offs. In
addition, an overall measure of discrimination across all possible cut-offs is the area
under the curve (AUC; reported as a c statistic or c-index in some studies), which
tests the probability that a randomly selected offender has a higher score on a tool
than a randomly selected non-offender. The curve is the Receiver Operating
Characteristic Curve (or ROC curve), which plots true positives against true
negatives. To take one example, an AUC of 0.70 is the equivalent of saying that that a
tool will correctly assign a higher score 70% of the time to a randomly selected
offender than a randomly selected non-offender. Many studies rely on simply
presenting discrimination statistics, and even then, only the AUC, which on its own is
uninformative. For example, a tool can correctly classify those into higher and lower
risk groups at all possible cut-offs, but is only used at a specific cut-off, where its
discrimination is much poorer. This can be exemplified in the case of a risk
assessment tool that has 30 items, and is scored from 0 to 30. If the tool is tested in a
research study, and it correctly assigns all the offenders with a score of 2 compared to
all non-offenders who score 0 and 1, then it will have a perfect AUC of 1. However,
the guidelines for the use of the tool state that a score of 5 and above should be used
to determine high risk of offending, and therefore the AUC statistic masks its poor
intended performance. If used as intended with a cut off of 5, this would mean that
everyone in the sample is assigned a low risk score, even though some of these
individuals are offenders. Depending on the number of offenders and non-offenders,
this would mean that the AUC is closer to 0.5 or chance. AUCs below 0.5 are worse
than chance – in other words, such models are systematically wrong. This is one of
the reasons why presenting a range of performance measures is important, particularly
true and false positives and negatives. Indicative values of good discrimination
measures have been discussed but there is no clear consensus (Singh 2013).
Further, an instrument may be accurate in identifying risk groups but do so in a
way that is very different to their real offending rates. In such a case, a tool may
estimate rates of offending of 10% to higher risk offenders compared to 9% to lower
risk offenders, and hence perfectly discriminates between these two groups. But if the
higher risk offenders are more likely to offend at rates of around 40% and the lower
risk offenders at 1%, then it is very poorly calibrated and has little if any practical
utility as a prediction model (Lindhiem, Petersen et al. 2018). Calibration refers to the
agreement between observed outcomes (i.e. offending) and predictions from a
particular tool. For example, if there is a prediction of a 30% reoffending risk
following release from prison in 1 year, the observed frequency for reoffending
should be around 30 out of 100 released prisoners with such a prediction.
Sensitivity (the proportion of people who have offended that an instrument
correctly classified as high risk) needs to be high if the aim is to screen individuals for
a disease (e.g. for further costly or more invasive investigations), and important from
public policy perspective as the consequences of ‘missing’ an individual who offends
needs to be considered. The corollary of sensitivity is the false negative rate (which is
calculated as 1-sensitivity) – the proportion of individuals who commit crimes that the
tool misses. A false negative rate of, say, 5% is equivalent to the tool not correctly
identifying 5 out of every 100 individuals who have offended. Specificity (the
proportion of individuals who have not offended that are correctly identified) should
be high if the implications of being labeled high risk are harmful (e.g. longer
sentences or preventative detention). The false positive rate is the inverse of
specificity (1-specificity) – the proportion of people that the tool incorrectly estimates
will commit crimes. The relative proportion of true and false positive and negative
rates will be determined by a range of legal, ethical and political concerns. Low false
negative and positive rates will clearly be preferred, but a high false positive rate
could be acceptable if the consequences of being labelled higher risk are not harmful.
To exemplify this, if a tool does not miss individuals who reoffend on release (low
false negative rate) but also identifies many people as high risk who do not reoffend
(high false positive rate), this is less concerning if the consequences for those
incorrectly identified as high risk are not harmful, such as additional support on
release. Where it will be problematic is if the high risk group have their prison
These decisions will need some alternatives to consider, such as the relative
balance without using such tools or two approaches can be compared. Some tools
have tried to maximize the combination of sensitivity and specificity by adjusting cut-
off points (e.g. looking at the inflection point of a ROC curve – the point at which it
has the highest true positive rates on the y axis and negative rates on the x axis). Here,
researchers would look at the best possible cut-off by looking at the inflection point.
By finding the inflection point, this will translate into a cut-off to the nearest whole
number for a tool that has the best discrimination for that particular sample being
studied. The problem with this approach is that it is unlikely to generalize to other
samples, and pre-specifying a cut-off is preferable methodologically. In other words,
taking this approach to identifying the best cut-off statistically will likely only apply
to the specific sample being studied rather than new populations.
Some commentators have suggested that positive predictive value (PPV; the
proportion of people that a tool identifies as high risk that actually offend) and
negative predictive value (NPV, proportion that are low risk that do not offend) are
more relevant to criminal justice as it is how these tools are used in practice
(Buchanan and Leese 2001, Coid, Ullrich et al. 2013). The main limitation with this
approach is that these two measures, alongside sensitivity and specificity, are also
sensitive to the base rate – so the PPV will be low if the rate of offending in the
population of interest is low, and the NPV will be high. Nevertheless, the NPV is
increasingly important in some countries where decarceration is a public policy
priority – which provides information on the proportion of prisoners that can be safely
released (i.e. not reoffend within a specified time period). It is also important for some
populations such as juveniles and women, where prison should be avoided if possible,
due to secondary effects on education, work, family and social networks, and mental
health (Abram, Zwecker et al. 2015). Sensitivity, specificity, PPV and NPV will
change if a tool’s cut-off changes – if the threshold for high risk increases, then
sensitivity and NPV will decrease, and correspondently specificity and PPV will
increase. This is one reason why the AUC is often presented as a summary statistic as
it presents measures of discrimination (sensitivity and 1-specificity) at all possible
cut-offs. At the same time, using AUCs to compare risk tools is problematic as very
different numbers of false negative and false positive predictions resulting from
different shapes of receiver operating curve may have the same overall AUC (Mallett,
Halligan et al. 2012).
The other key measure of a tool’s performance is calibration. This asks how
closely the tool’s predicted risk matches the observed risk. For example, a tool that
predicts a 20% chance of offending in a particular sample, but only 10% actually
offended, is poorly calibrated. Calibration can be examined graphically by plotting
predicted risk versus observed offending behaviour or through statistical tests to
measure the typical level of miscalibration, such as the Brier test or HL statistic
(Lindhiem, Petersen et al. 2018). Calibration is the key performance measure if only
probability scores are used – as the discrimination measures are only possible if there
are a limited number of cut-offs. One important area of contention relevant to
calibration is the group to individual problem – and proponents of this view have
argued that it is not possible to apply group information to individuals due to lack of
precision, also known as the G2I (‘group to individual’) problem. The argument is put
forward that when an actuarial tool provides a probability score of 30%, applying this
to an individual is subject to the potentially large variation underlying the probability
score. Hence 30% actually means 10-50% for an individual and hence not
informative. However, this view is based on a misunderstanding of statistics – all
individual predictions are based on group data, and their precision will be a
consequence of sample size (Imrey and Dawid 2015). The probability score of 30%
for a risk assessment tool can be interpreted by stating that it refers to an individual
with the same risk factor profile who will on average reoffend at a rate of 30%.
The overall performance of currently used risk assessment
So what do we know about the performance of currently used tools in criminal
justice? There have been a number of systematic reviews that have outlined their
performance. Interestingly, none of them has reported calibration statistics as it seems
that this is very rarely reported in the research literature. In fact, one 2013 review of
how AUCs were presented in 50 studies did not report one calibration metric (Singh,
Desmarais et al. 2013). The review by Yang and colleagues in 2010 looked at head to
head comparisons of 9 violence risk assessment tools, and identified 28 studies in no
more than 7221 individuals, that reported AUCs and a measure of effect size
(Cohen’s d). It concluded that there was little difference in the included risk
assessment measures, which varied in AUCs between 0.65-0.71 (Yang, Wong et al.
2010). A later and more comprehensive review of an overlapping but different set of 9
instruments identified 73 studies including 24,827 people (Fazel, Singh et al. 2012).
This review presented a broader range of discrimination statistics – and also
separately by violent offending and any criminal offending. The findings were
different by type of predicted outcome – for violent crime, sensitivity was high (0.92)
and specificity low (0.36), with moderate PPV (41%) and high NPV (91%). For any
offending, sensitivity was low (0.41) and specificity high (0.80), with moderate PPV
(52%) and NPV (76%). In terms of AUCs, for violent offending it was 0.72 and for
criminal offending it was 0.66. Overall, these are mixed discrimination metrics –
moderate AUCs and NPVs, and suggest that their use in practice needs to reflect these
differing performance metrics. One possibility is to screen out low risk offenders.
Another is to solely use these tools as adjuncts in the decision-making process due to
positive predictive values of around 40-50%. Finally, due to the low specificity of
violence risk assessment, they should only be used when the consequences of high
risk categories are non-harmful interventions, such as additional management or
treatment. Another way of looking at these findings is to focus on false negative and
false positive rates – for tools predicting violent outcomes, it was 8% and 64%,
respectively; for tools predicting any criminal outcomes (such as LSI-R), it was 59%
false negative and 20% false positive. If the implications of false positive rates are not
harmful, this would suggest that instruments predicting violent outcomes should be
prioritised over those focusing on any crime. In other words, this review found that
the balance between false negatives (low for tools focusing on violent crime but more
than 50% for tools with any crime outcomes) and false positives (high for tools
focusing on violent crime but lower in those predicting any crime) favours the violent
risk assessment tools if the consequences of false positive (i.e. being labelled high risk
and not reoffending) are not harmful. The 59% false negative rate for tools predicting
any crime is arguably too high for their widespread use in criminal justice.
A third notable review summarised research on the predictive validity of 19
instruments used in US corrections from 1970 to 2012 (Desmarais, Johnson et al.
2016). This review underscores the problems with the reporting of this literature. It
found that only summary statistics were presented and solely for general recidivism
(as distinct from violent recidivism). The median AUC of these tools typically ranged
from 0.64-0.71 for new offences, and in real-life settings, the Level of Service
Inventory (LSI-R), which is a commonly used tool, had an AUC of 0.63 and the RMS
an AUC of 0.66. As with the other reviews, no information on calibration was
reported, which is problematic as all the 19 included tools provide probabilistic scores
of reoffending (and, in some cases, parole violations).
Overall, based on these recent systematic reviews of current risk assessment
tools, there are problems in how these instruments are reported, with insufficient
information on their performance. In addition, there are other problems with
transparency . The statistical contribution of individual risk factors to the final model,
and the process by which they were chosen and categorised should be outlined. This
transparency is important as it allows for the models to be critically appraised by
experts, such as the nature of the sample that it was derived in, the choice of
predictors and how they were categorised, the statistical power of the study, and the
precision of the performance measures. This is particularly important if harm follows
from a tool’s use, such as longer sentences, certain interventions, and more
restrictions in the community . Another problem are the potential financial and non-
financial conflicts of interests among researchers in this field, and many of the tools
being studied are conducted by individuals who developed or translated them (Singh,
Grann et al. 2013). Such potential conflicts need to be disclosed, which currently
Scalability and cost need to be considered – some of the tools have commercial
licences (such as the COMPAS or Correctional Offender Management Profile for
Alternative Sanctions), which takes up to 60 minutes to complete. Many of these tools
also assess individual needs and treatment (and linked to responsivity, which is the
extent to which an intervention is responsive to the individual needs identified), and
their predictive validity is one element in their potential value. However, conflating
risk and needs can lead to loss of performance on risk, and empirically robust risk
calculators are required before more careful assessment of needs and treatment.
Further, there have been some recent attempts to focus on causal risk factors as these
will lead to reductions in recidivism once treated (Howard and Dixon 2013).
However, one problem with this approach is that the most predictive factors (eg age,
previous crime) are not causal, and excluding such factors will lead to poorer
performance in terms of prediction. If the next stage of any risk management process
is needs assessment, then identifying causal risk factors will be informative but will
require different approaches (such as quasi-experimental designs and treatment trials
rather than correlational studies of risk factors). Another issue is that the performance
of current tools shrinks when used in real-world settings as distinct from research
studies. A recent example was reported for the commonly used Psychopathy
Checklist, revised edition (PCL-R). In a field trial in Belgium, its predictive validity
was poor with an overall AUC of 0.63 for general recidivism and 0.57 for violent
recidivism (Jeandarme, Edens et al. 2017), which compares unfavourably to mostly
research studies that have reported higher AUCs of 0.66-0.67 (Singh, Grann et al.
2011) (Yang, Wong et al. 2010). The Level of Service Inventory (LSI-R), when used
prospectively in over 22,000 prisoners in Washington State, USA, was associated
with an AUC of 0.64 for violent recidivism (Barnoski and Aos 2003), which is lower
than its performance in psychiatric samples and research studies. This shrinkage is a
consequence of a number of methodological weaknesses in the design of these tools
(see below for LSI-R).
A practical guide to evaluate risk assessment tools
So what to make of this in practice? How can individuals in criminal justice and
public policy determine whether a tool is fit for purposes? We have proposed a ten-
point guide (Fazel and Wolf 2018), which I will summarise. I will start with criteria
relevant to the derivation (or discovery or development) study, and then move on to
criteria relating to the validation of risk assessment tools. The relevant criteria are:
1. Did the study deriving the tool follow a protocol?
This is a key component if a study is to provide an accurate representation of a tool’s
performance. Without a protocol, the likelihood of creating a tool that reports strong
performance measures but performs poorly in practice is very high. The sample,
candidate variables, outcome(s), follow-up periods, statistical analyses, and output
should all be pre-specified before any data analysis is performed. This protocol
should be published, and any deviations from it in any particular study be clearly
explained and justified (such as a predictor being dropped because of large
proportions of missing data).
2. How were candidate variables selected for the tool?
The more variables that have been tested in a derivation study, particularly if the
sample was not sufficiently large, the more likely chance associations are found, and
the reported model performance will not perform well in external validation. One
rule of thumb is that for each variable tested the derivation sample should have at
least 10 outcomes (Royston and Sauerbrei 2008). Further, the choice of which
variables to test and how they are categorized should have followed a protocol, and
multivariable regression should have been conducted to determine their independent
association with the outcome before inclusion in a model. Otherwise, tools will
include variables that do not add incremental predictive accuracy, and lead to over-
complicated and time-consuming instruments.
3. How were variables weighted?
Many tools in criminal justice give equal weighting to all included items. This
makes two assumptions – first, that all included predictors have the same association
with the outcome, and second, that the variables are all independently related to the
outcome. In terms of weighting, previous violent crime and living in a poor
neighbourhood are both associated with higher risk of crime, but they are not
equally important. Tools that have not weighted individual items will perform worse
(Hamilton, Neuilly et al. 2015).
4. How were other parameters selected?
Other key aspects of any research study should be determined beforehand, such as
the time for follow-up for the tool. If this has not been done, to take an example, a
particular tool may perform better at 3 years rather than 1 or 2 years, and the
researchers might decide that 3 years is the primary outcome. The problem with this
approach is that it is a form of multiple testing and the consequence will be that the
tool performs considerably worse in real-world settings.
5. Has internal validation been done?
This is typically done using a method called bootstrapping, which takes a number of
random samples from the dataset to provide an estimate of accuracy of performance
6. Has the tool been externally validated?
This question examines whether the tool’s performance has been investigated in a
new sample. In many ways, this is the most important question as tools tend to
perform considerably better in the sample in which they were derived (Khoury,
Gwinn et al. 2010, Monahan and Skeem 2016) and an external validation is
necessary to test how accurate it is. Splitting the original derivation sample into two
random groups is a form of internal validation, but is not external validation due to
the equal distribution of predictor variables. Such a split will lead to comparable
performance because the predictors will have a very similar distribution in the
derivation and the randomly split samples. To achieve external validation, the
sample should be split on other variables, which are not related to the outcome
(Fazel, Chang et al. 2016).
7. Has this validation been done in the population of interest?
Here the key issue is whether the new population for which the tool will be used has
similar characteristics, risk factors, and baseline risk, and outcome to the sample
where the tool was created. This may explain why some tools, such as the PCL-R,
which was not developed to predict violence risk but to identify a form of
personality disturbance, performs among the worse of commonly used tools (Singh,
Grann et al. 2011). In addition, this is problematic for some tools developed in
selected samples of high-risk offenders (which appears to have been the case for
LSI-R) that are then used in general criminal justice samples, such as all individuals
in prison or on probation.
8. Has the validation been conducted using robust methods?
Validation studies should stay true to the original model, be based on a protocol, and
anticipated changes should be discussed beforehand in a protocol (eg recalibration
will be considered if the underlying base rate of offending is different, and how this
recalibration of the model will be tested). Otherwise, what appears to be a validation
is no longer an external validation, but the derivation of a new model. The sample
size is also important, and should have ensured at least 100 events (or outcomes) for
statistical power (Collins, Ogundimu et al. 2016). Results should be published in
peer-reviewed journals, but, on its own, this is not a marker of methodological
quality. Studies should provide sufficient methodological detail to be replicable.
9. Has the validation study reported essential information?
As described above, tools should report both measures of discrimination (especially
rates of false positives and negatives) and calibration (ideally with a graphical plot
that compares observed with predicted risks).
10. Is the risk assessment tool useful, feasible, and acceptable?
The tool should provide useful information including a relevant outcome (eg
positive prediction of reoffending), and clearly defined risk categories. The tools and
their constituent predictors should be also be easy to complete, reliable and clearly
defined. For example, rating scales (e.g. 1-5 Likert scales) will be may vary between
raters. The tool should have face validity by including essential items (for example
age and sex), and justify the inclusion of other items. There are advantages in having
interview-independent tools to reduce the possibility of observer bias.
If a particular tool has not been externally validated, we argue that it should not be
used in practice apart from rare circumstances when alternatives are not appropriate
or available, and external validation is ongoing (Fazel and Wolf 2018). And even if it
has been externally validated, instruments should undergo prospective validation after
implementation to monitor their ongoing accuracy.
Applying quality criteria to individual risk assessment tools
The extent to which risk assessment tools currently used in criminal justice meet these
10 criteria needs to be systematically evaluated but few of them meet more than one
or two. To take some examples of commonly used tools, on these five criteria for
derivation discussed above, two such instruments, the HCR-20 (Historical Clinical
Risk Management-20) and VRAG (Violence Risk Appraisal Guide), meet few
criteria. The HCR-20 chose its 20 predictors based on expert opinion in 1997 rather
than a systematic review of the evidence or testing them in multivariable models (an
approach the authors reported in the following way: ‘What variables might clinicians
and administrators consider as they attempt evaluations of risk of violence in cases
where psychiatric disorders are thought to be involved?’) (Webster, Douglas et al.
1997, p. 251). The derivation did not include any statistical performance measures.
Each item is scored as ‘0’ (item not present), ‘1’ (item possibly present), or ‘2’ (item
definitely present) rather than assigning any weighting to them (Douglas and Reeves
2010). Age and sex, two of the strongest predictors of violence and considered
important for face validity, were not included. In developing the VRAG, 42 candidate
variables collected from a single sample of 618 mentally disordered Canadian
offenders (of whom 191 reoffended). Of those, 332 individuals had been received into
a maximum-security prison, and the remaining 286 had been admitted to secure
hospital for a brief pre-trial psychiatric assessment. With regards to the outcome, 191
reoffenders does not provide sufficient statistical power for 42 candidate variables
(Harris, Rice et al. 1993), and good practice would suggest that at least double the
number of reoffenders would be required for derivation. The VRAG’s derivation
study reports performance measures at five different cut-offs (which were not pre-
specified), and does not provide an overall performance measure. As with the HCR-
20, the offender’s sex was not one of the variables considered and hence was not
included in the final model, which consists 12 items, which are weighted.
Two other widely used tools are difficult to evaluate due to lack of published
information about certain aspects of their derivation and original validation. The LSI-
R is based on 54 dynamic items, and the OASys Violent Predictor (OVP) in England
and Wales, which is given to all individuals who receive sentences of 12 months or
more, and derived from the 100 item OASys (Howard and Dixon 2012). The LSI-R,
however, does not include some of the most powerful predictors such age or gender,
and has items that appear to be unreliable psychometrically (such as ‘could make
better use of time’, has ‘very few prosocial friends’ and four items on current
attitudes). Importantly, the original derivation study has not been published to my
knowledge. The OASys is better reported and has some selected publications
explaining aspects of its derivation, but lacks detail on some key areas (Howard and
Dixon 2011, Howard and Dixon 2013). At the same time, both LSI-R and OASys
have weighting for individual predictors that were tested using logistic regression in
developing the model, relatively simple scoring methods, and been subject to external
Putting this altogether, I would argue that the most commonly used tools in
criminal justice are not fit for purpose for prediction purposes. None of them meet all
the 10 tests outlined above to my knowledge, and few meet more than one or two of
the criteria outlined. At the same time, some of these instruments may provide a
useful framework for organising information, act as a reminder for those working in
criminal justice to assess certain risk factors and domains, and match individuals for
treatment based on needs. The first two of these justifications are arguably too high a
price to pay for those instruments that are resource-intensive.
After reviewing this literature, I have been part of a team that has developed OxRec
(Oxford Risk of Recidivism tool), using Swedish national data, which provides a
probabilistic score for violent and any reoffending in 1 and 2 years post-release from
prison, and also low/medium and high categories based on pre-specified levels. It can
be completed in 5-10 minutes using 14 routinely collected predictors, and using a
freely available online calculator (Fazel, Chang et al. 2016). The weighting of the
individual predictors and how they are combined to create a probability score has
been published (with the original protocol), with a full range of discrimination and
calibration statistics, making it a fully transparent risk prediction model. It has been
externally validated in Sweden in more than 10,000 individuals leaving prison, with
ongoing validations in the Netherlands and some other countries (Fazel 2019), and
provides a methodological rigorous approach with which to develop risk assessment
instruments. The probability score is relatively precise as it was derived on 37,100
In summary, I have outlined some key ways of evaluating the performance of risk
assessment instruments in criminal justice, and highlighted the importance of both
investigating measures of discrimination and calibration. I have outlined some
systematic reviews of the field, which suggest that many current tools, such as the
LSI-R and PCL-R, have at best moderate performance in discrimination with no
information on calibration. Most tools currently used in criminal justice have not been
included in these reviews because research on their external validation has not been
published. Further, the development of risk assessment tools in criminal justice has
lagged behind methodological improvements in prognostic models in science, and
particularly in medicine.
Finally, I have provided a ten-point checklist that can be used to evaluate any
risk tool. On this basis, I have argued that current widely used tools should probably
not be used for prediction. At the very least, their use be reviewed in the light of the
ten tests outlined, and information that is lacking should be requested from these
tool’s developers and commercial entities marketing them. In terms of its implications
for predictive sentencing, risk predictions from these tools - either as categories such
as high, medium or low, or as probability scores – do not have a sufficient evidence-
base in support that they can currently be used in court. As I have shown, current risk
assessment tools have not met some basic criteria in how they were derived or in
subsequent validations of their performance. Furthermore, when empirically-tested on
a range of measures and mostly in research studies, they typically lead to
unacceptably high false positives and false negative rates, particularly in tools aimed
at any recidivism. I have also discussed the development and validation of a new
scalable prediction tool, OxRec, which represents a methodological advance and
provides a model for transparent reporting of such tools.
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