More Polygraph Futility

Introduction

Jensen, Shafer, Roby, and Roby’s (2015) recent article published in this journal purportedly examined and found no differences in failing sexual history polygraph examinations between juveniles and adults drawn from polygraph testing. However, my reading of the evidence they present identifies no such justifiable conclusion based on the data and analyses they present in their article. I detail my interpretation of their evidence below, but quite simply this study used a small, nonrandom sample of juvenile and adult sex offenders tested by one polygrapher in one agency, so it is more an assessment of the consistency of that polygrapher than it is of age differences. More importantly, no assessments of efficacy or effectiveness in reducing recidivism from sexual history polygraph disclosure can be drawn with the results they provide. Hence, there are no generalizations that can be drawn from their sample, and it does not support their conclusion that “juvenile and adult sex offenders appear to generate similar outcomes in sexual history polygraph examinations” (p. 941).

Before I give my criticisms of the article, it needs to be stated again that post-conviction polygraph folks keep hyping increased disclosure by offenders as an outcome when the real outcome should be whether or not increased disclosures translate into reductions in reoffending (Rosky, 2013). Even Jensen et al. (2015) state that post-conviction polygraph testing is supposed to “improve treatment outcomes” (p. 931). So as Rosky (2013) and others have argued previously, if it does then great; if it does not, then it is a useless exercise that can mislead clinicians and probation and parole officers into treatments and sanctions from false positives that are unnecessary (e.g., wrong therapies) and costly (e.g., revocation and reincarceration) or worse, allow further victimization to occur from false negatives. Here, the authors offer nothing in this article to help determine whether post-conviction polygraph testing “works” to reduce offending.

A Critical Review of Jensen et al.’s Article

Beyond the lack of any adequate behavior outcome, my first concern with the Jensen et al. (2015) article is that the authors do not seem to understand basic research concepts such as independence. For instance, they claim that “more than 99% of the cases in our sample were assessed by the same polygraph examiner. This condition greatly reduced the likelihood of nonindependence among individual observations” (pp. 936-937). No, there is no reduced likelihood of dependence. Subjects shared the same polygrapher, so the results have internal correlation because they were measured by the same person; that is, their sample consists of repeated measures by one polygrapher in one agency. After their above statement, they do go on to say that they do not have enough polygraphers to use a hierarchical analysis that would be needed to account for repeated measures variation, but not being able to do a particular analysis to account for certain types of variability does not mean that type of variability does not exist and does not affect the analyses. What do the authors think would happen if they were to use multiple polygraphers and agencies? Do they really believe that polygraphers, agencies, and offenders would be the same across all of those entities and would not vary without first verifying that assumption? More importantly, they included no evidence regarding their lone polygrapher, including his or her training, educational background, professional history, and experience as a polygrapher. Were there differences in disclosure rates for race or ethnicity as there were for gender? Were there differences for type of offender (i.e., rapists vs. molesters vs. child porn consumers)? These are significant omissions by the authors and do not help the reader in understanding these results in a broader context. Most importantly, the data, being wrought from the same polygrapher, are really a measure of that polygrapher’s consistency for failing subjects across ages than they are a measure of failure rates across ages. Quite simply, we know that the polygrapher can affect test outcomes by his or her demeanor, training, and experience (Heil & English, 2009), so this sample can tell us nothing about whether failure rates are the same across ages without additional polygraphers to see if the fail rate holds the same across polygraphers and ages.

My next concern is how Jensen et al. (2015) use age in a manner that does not account for the significant physical and cognitive variation that occurs in the aging process, especially for juveniles, and ignores established research regarding the age–crime curve. That the age range for juveniles in this study is 11 to 17 coupled with the uncontested fact that an 11-year-old is not developmentally the same as a 17-year-old either mentally or physically causes me great concern. As others have also argued before (Rosky, 2013), this goes to the heart of what post-conviction polygraph testing is trying to do with getting offenders to admit their past sexual offending—estimate an offender’s criminal career in sex offending. Does it make sense to assume that an 11-year-old would have a similar sexual or criminal history length as a 17-year-old, a 25-year-old, or an 83-year-old? Common sense and research tells us the answer is no; offenders will have different rates of what they can lie about based on their age alone—young offenders will have shorter and less varied criminal careers along with less opportunity than adults, notwithstanding a few precocious offenders (DeLisi, 2005). Hence, the authors’ age variable is significantly confounded by its relationship with human development and opportunity for sexual and criminal encounters. Without adjustments for these confounders, the unadjusted use of age in their analyses is misleading because variation in criminal and sexual history grows, both in breadth and depth, with age. Moreover, their statistical analyses were done on a small, nonrandom sample, so the usual interpretation of p values cannot adequately judge statistical significance (Gelman, 2013). What I conclude from their logistic regression is that there is a small but variable effect of age that shows that the likelihood of passing a sexual disclosure polygraph test grows minimally with age, which is what their descriptive statistics also show where juveniles passed at a 67.4% rate and adults passed at a 68.5% rate. However, my interpretations are tempered by the lack of known criminal and developmental correlates within either of their analysis. Note that dichotomizing age into juveniles and adults also ignores the significant physical and cognitive variation that occurs in the aging process because juvenile status is a legal definition and not a developmental definition. In this case, a simple histogram of age by disclosure status (deceitful/truthful) would be more informative rather than hiding behind p values as it would show the variability of fail/pass across ages. In addition, Jensen et al. (2015) cannot say what the base rate of deceit is within age, so there is no way to also ascertain that the rates of deceit are the same across ages. Hence, their analyses of age are overly simplistic, are not robust estimates of age effects either statistically or practically, and are not good evidence for a null effect regarding failure rates across ages.

In addition to my concerns over Jensen et al.’s (2015) age variable, I am also skeptical of their measure of deceit. They state,

In some cases, clients would not pass their polygraph examination, meaning that they were found to be deceitful to at least one of the three yes-or-no questions asked by the examiner. The examiner would then either issue a second test in the same session after the client disclosed more information, or the client would prepare for another examination in the near future (at least 30 days later as required by state law). If the client was issued two tests in the same session, we used any indication of deceit as the outcome, regardless of it being the result of the first test or the second polygraph test. In cases where individuals were required to prepare for an additional full-disclosure polygraph examination because they did not pass, we used the first polygraph exam issued for our analyses. If the first full-disclosure polygraph had results which were deemed inconclusive or incomplete, we used the next polygraph exam issued (this specific scenario only occurred once among those in our analytical sample). For individuals who passed their polygraph examination, no further action was taken in terms of additional examinations. (p. 934)

Several questions come to mind with this paragraph. First, whywere offenders who “passed” the test on the first go-round not given a second test? This effectively bifurcated the sample because failures were treated differently right off the bat and we have no way of comparing those who passed on the first go-round with those who passed on the second. In other words, how many of them would fail this second test after passing the first? This alone would give us some sense of test failure variation. Next, how many tests were inconclusive or incomplete? Of the offenders who “failed,” how many did so on one, two, or three questions? Did they fail the same question(s) in the second or subsequent test? But most importantly, what questions were shared across offenders? It seems reasonable that some passed merely because they were not asked the right questions about their sexual histories. In addition, were there differences in sociodemographic characteristics (other than age and gender) between those who passed on the first try and those who did not? Another necessary assumption beyond independence of observations is that these observations are also identically distributed, that is, they are generated from the same random process (Agresti & Finlay, 2009; Hogg & Craig, 1994). As the authors noted in the above-cited paragraph, this is not the case here because of the varying ways that deceit is captured. The authors should have included all of these results to present a more complete picture of their deceit variable because there is significant variation in how deceit was measured that is not demonstrated in their presentation of this variable.

In addition to construct validity issues, along with the admittedly unknown base rate, the accuracy of post-conviction polygraph has not been conclusively established, especially in screening applications such as sexual history disclosure (Rosky, 2013; U.S. National Research Council, 2003). However, using the authors’ results that the test (in reality, the polygrapher) indicated 103 were deceitful and 221 were truthful in their disclosure of sexual histories, we can create differing scenarios assuming a given base rate of deception. For instance, if the base rate of lying in their sample is low, say 10% (e.g., 32 of 324 were actually lying) and the test is 85% accurate, ¹ then 27 of the 32 who were lying would be correctly identified. But it would also mean that only 27 of the 103 the test identified as deceptive were actually deceptive. In other words, the test would have a 78% false-positive rate and wrongly place offenders in a particular treatment or be falsely accused of noncompliance. If we increase the base rate of deception to 33% given in the article, then the test would be fine with both reasonably ² low false-positive and false-negative rates; but if the base rate was 50%, this would mean that 162 offenders are deceptive yet the test only identified 103 as deceptive, and I assume that the authors would agree that 103 is not 85% of 162. But even if we were to grant that all of the 103 the test identified as deceptive were correct, then it would falsely identify 59 deceitful subjects as having truthful disclosure. Hence, they would not get the proper therapy or supervision level and thus have an increased risk of creating new victims. Moreover, this false-negative number only grows larger as the base rate of deception grows larger. Again, this is why knowing the base rate and accuracy is so critically important because even with supposedly high accuracy, post-conviction polygraph testing leads to higher false positives (wrong therapies, increased costs) if the base rate is low and higher false negatives (increased victimization) if the base rate is high. I hope that the authors and other proponents can see why knowing the base rate is such an important part in evaluating this treatment and should be part and parcel of any assessment.

Responding to Jensen et al.’s Recidivism Arguments

Here, beyond the results of their study, Jensen et al. (2015) proffered three arguments refuting the notion that linking disclosure with recidivism is really the only way to assess post-conviction polygraph testing. In their first argument, they appeal to the “dark figure of crime” (Biderman & Reiss, 1967) in that the true recidivism rate can never be known and thus is a poor way to assess the utility of polygraphy. I agree that the true rate can never be known but that is irrelevant to the issue here as to whether post-conviction polygraph helps lower recidivism. Quite simply, having imperfect measures that undercount true recidivism does not obviate the need to show that post-conviction polygraph tests have some impact on the underestimated rate. I am pretty sure that if post-conviction polygraph proponents could show a decrease in imperfect recidivism there would be articles trumpeting the reduction in recidivism rather than the significant amount of articles trumpeting that it increases the disclosure and is well liked by therapists, correctional staff, and offenders. Also, recidivism is not just defined as being convicted of a new crime; it can also be measured by arrest and technical violations which when used with new convictions provide a much broader view of recidivism (see Hamilton & Campbell, 2013; Lutze, Rosky, & Hamilton, 2014; Wright & Rosky, 2011). Moreover, we certainly do not need to know the exact number of times an offender has recidivated to determine whether an intervention worked to reduce recidivism for a given population. For instance, failing a drug test does not measure how many more times an offender may have used drugs beyond the one failure, but it sure can tell us if certain types of substance abuse treatments worked to lower violations that multiple offenders passing an imperfect drug test in such treatments would indicate. Moreover, their argument ³ that recidivism “still fails to account for all possible future behaviors that are sexually unlawful” is merely an appeal to ignorance because recidivism is not a future measure (p. 939, emphasis in original); it is a historical measure of actual behavior. I surmise what the authors are arguing here is that disclosure changes risk for future recidivism but if we cannot measure all recidivism, then recidivism is a useless way of assessing whether the polygraph works to lower recidivism. That is a nice, round argument, but if that is the case, then we should not believe any evaluation that uses recidivism as an outcome measure. Surely the authors would agree with that, right? But then we would have to ignore the plethora of evidence in the “what works” literature (MacKenzie, 2006) that uses recidivism as an outcome to assess efficacy and effectiveness of those interventions and programs that have been shown to reduce future criminality, including cognitive behavior therapy, therapeutic communities, and vocational/educational programs. It would also dismiss the evidence against those that do not work or may increase recidivism, including boot camps and Scared Straight programs, and allow these types of correctional quackery to once again become more prevalent than they already are. Again, as has been stated before (Rosky, 2013), correctional treatments and interventions that are designed to change behavior have to measure that change, however underreported it may be. Polygraphy should not be treated any differently than other correctional interventions nor should we lower our expectations as to what constitutes good evidence.

In their next argument, Jensen et al. (2015) claim that those of us who take a critical look at post-conviction polygraph use are ignoring the breadth of research, showing that offenders, correctional staff, and therapists think that polygraph is a useful tool in therapy. This is clearly a straw-man argument as we argue that proponents need to demonstrate efficacy and effectiveness before they assess popularity. The authors also posit a false dichotomy between what they called subjective client assessment and objectively demonstrated efficacy where they ask whether one is superior to the other. Before I answer this in the affirmative, the word objectively should be replaced with systematic because not even the scientific method is completely objective; it is an endeavor fraught with human frailty and bias that requires reliable replication to overcome these issues. But to answer their question regarding the superiority of systematic evidence of behavioral change over evidence of popularity, yes, because subjective perception of benefit from a therapy or intervention without also showing replicated and robust efficacy and effectiveness for that therapy or intervention means that we are wasting time and money on a tool that does nothing to change behavior and increases the likelihood of victimization. Again, polygraphy does not get a pass on assessing its efficacy and effectiveness as a correctional intervention.

Their third and final argument states that the burden of proof for polygraph testing’s efficacy and effectiveness should be on those questioning its efficacy and effectiveness rather than its proponents. This is essentially arguing that we proponents are right until you critics prove us wrong. But that is not how science works; the burden of proof is on those making the claims and not on the ones who point out problems with claims. Moreover, this is the same gambit used by psychics, faith healers, snake oil salesmen, and homeopaths against their critics who point out deep flaws and lack of evidence for these types of quackery (Randi & Sagan, 1987; Shermer, 2001). So the burden of proof is on the proponents of polygraphy and, at the risk of sounding like a broken record, they need to show good, reliable, replicable evidence of the behavioral change from the intervention.

Finally, there are two threads woven through these three arguments that need to be debunked. The first is that those of us who are critical of post-conviction polygraphy ignore its potential benefits for clients. But nowhere in Jensen et al.’s (2015) arguments do I see discussion of the potential harm for clients in being forced into needless therapy or sanctions, the potential cost to the system for needless treatment and sanctions, or the potential harm to victims from false negatives. You cannot claim benefits without also claiming the costs, and that is what critics of polygraphy are trying to get proponents to understand. Indeed, who is really ignoring evidence here? Those of us who are critical of polygraphy are taking an all-inclusive approach that requires solid evidence from sound, replicated research before we are willing to accept any correctional intervention, not just polygraphy. These small, nonrandom studies, whether they assess outcomes or not, simply are not good evidence and no sound research-oriented argument can be made otherwise.

The second thread is the implication that we critics do not care about the welfare and treatment of offenders. On the contrary, I care deeply about the welfare of offenders that includes humane, ethical punishment and treatment. Although I cannot speak for others, I am confident that these other critics feel similarly. Indeed, this perspective of ethical treatment guides my research philosophy in that I seek with my research to broaden knowledge, create better policies and more humane practices, and improve our methods for understanding our field and discipline. I believe that polygraph proponents feel the same. More importantly, if there was sound, reliable, and replicable research in favor of post-conviction polygraph, I would willingly accept it. However, I am not sure if proponents of polygraphy would accept evidence that post-conviction testing does not work in aiding therapeutic outcomes, given their large focus in the literature on demonstrating offender, clinician, and correctional subjective belief in its utility rather than systematic outcomes such as recidivism.

Evaluating New Empirical Research on Polygraph and Sexual Recidivism

Here, rather than keeping the presumption that proponents are uninterested in assessing recidivism I stated above, I searched for recent studies on post-conviction polygraph testing that utilized recidivism to assess its utility beyond what was included in Rosky (2013) and found only two studies in recent years that do so. Interestingly, both were attempting to determine whether sexual history disclosure from polygraph testing reduced recidivism. The first, a peer-reviewed article ⁴ by Cook, Barkley, and Anderson (2014), examined a small, nonrandom sample of 166 male sex offenders who came from “a single community corrections office in one rural Oregon county” (p. 4). They also measured recidivism as new convictions observed between 1999 and 2004. The first real issue occurs in their subsequent analyses of this sample where they did not attempt to match offenders between control and treatment groups via propensity scoring or other matching techniques needed to account for known confounding and bias from unbalanced factors and covariates (Stuart, 2010). However, they did have a risk-for-recidivism scale, Static-99 scores, for both groups and found that the nonpolygraph control group had higher mean scores than the polygraph treatment group which they then perplexedly compared only the recidivists in both groups and found no difference in scores. Great, the Static-99 worked to identify recidivists in both groups equally. Yet, the troublesome fact that having more high-risk offenders in the control group than in the treatment group was not accounted for in subsequent analyses, although it clearly should have been. When they analyzed recidivism using chi-square tests they found, unsurprisingly due to the higher proportion of high-risk offenders in the control group, a significant difference between the two groups in favor of treatment. To be clear, not including any risk adjustment for the very apparent differences in risk levels between treatment and control in this analysis alone calls into question anything presented in this study. Moreover, they also did not account for risk level in their analysis of time to recidivism with a t test that found no significant difference. Besides the problematic issue of a greater proportion of higher risk offenders in one group than the other, simple chi-square and t tests are not appropriate for time-to-event data, which should be done with survival analysis techniques such as Cox proportional hazard models that can account for the skewed time-to-event data and include other variables to control for their influence on recidivism (Allison, 2014). Hence, these serious and widespread statistical and conceptual problems mean that none of their conclusions in this article can be relied upon to determine the relationship with recidivism between those who have undergone sexual history polygraph testing and those who have not. It is simply not good research, and these issues should have been caught and fixed at peer review before publication.

The second study was from a dissertation ⁵ by Konopasek (2011) that examined the relationship between recidivism and timely sexual history disclosure using, similar to Cook et al. (2014), a sample of 192 sex offenders in Oregon. However, there is one notable difference in this case: The sample was drawn from a treatment office owned and operated by Konopasek. Before I go into my assessment of this research, it gives me no pleasure that I need to state up front that this dissertation contained numerous problems with its research strategy and analyses that would require significant changes in the setup, methodology, and analyses to make it worthy for consideration of publication in a peer-reviewed journal. These issues, which exist throughout the dissertation and should be readily apparent to anyone with a basic research background, harpooned any meaningful inference for which I give only a few examples below. I encourage readers to look at the document rather than solely relying on my description. Keeping that in mind, recidivism was measured as a new sex offense conviction over a 10-year period between 1994 and 2004. Interestingly, the majority of new sex offense convictions, about 45%, were for failure to register as a sex offender. I am not sure how failure to register as a sex offender is a sexual offense rather than a status offense, but Konopasek did omit these and other nonsexual offenses from subsequent analysis leaving a sexual recidivism rate of 6% or 12 of 192 offenders with new sexual offense convictions. In assessing this research, I first went to his logistic regression results predicting sexual recidivism that contained a number of demographic (age, race, gender), criminal history, and risk (psychopathy, Static-99) variables along with two disclosure variables of interest, full sexual history disclosure from polygraph and timely sexual history disclosure from polygraph. So far, so good—Konopasek (2011) included pertinent social, criminal, and structural variables needed in any model testing recidivism. However, I then noticed an absurd odds ratio value of 5,541,762.85 for gender in the table, meaning that males were 5.5 million times more likely to recidivate than females. Nothing was statistically significant in the model but I also noticed that the intercept estimate had a value of −17.7, which meant that the offenders it represented were 48.6 million times less likely to recidivate, and all of this was from a sample size of 192 subjects: 10 females and 182 males. You do not need to be a math wizard to see that it is difficult to get oddsratios in the millions from 192 subjects to recognize fundamental problems with the analysis. I then figured out that because the base rate of recidivism was low, 12 male-only offenders or about 6% of the sample, the model had a zero-cell problem due to having no female recidivists, so the numerical method used to calculate model estimates could not converge. Hence, these meaningless estimates were due solely to the software quitting its routine rather than getting caught in an infinite loop.

I then looked at Konopasek’s (2011) descriptions of his variables along with his bivariate analyses. Here, I discovered that his two variables of interest, full sexual history disclosure from polygraph and timely sexual history disclosure from polygraph, were functionally dependent, that is, timely disclosure could only be coded yes if disclosure was yes. This meant that, in addition to the zero-cell count problem above, he also introduced a functional dependency into the logistic regression by including both variables in the model. He also apparently included missing Static-99 data for females (coded 99 for missing), which meant that the logistic regression took these missing values to be real and 11 times riskier than the maximum value of 9 for males, certainly biasing the results. Finally, while he found no statistically significant relationship between disclosure and sexual recidivism, first in his bivariate analysis and then in his initial logistic regression, he kept at it, running a stepwise logistic regression ⁶ that whittled down the original 13 variables to only 7 and found a statistically significant relationship between recidivism with timely disclosure and age at full disclosure. Here, timely disclosure seemingly reduced the risk of sexual recidivism fourfold, whereas age at disclosure increased the risk of sexual recidivism sevenfold for every year an offender aged. The latter result is perplexing, giving the ample criminological evidence that older offenders have decreasing recidivism risk as they age (DeLisi, 2005). Interestingly, the intercept estimate remained −17.7, which indicated that these offenders still were 48.6 million times less likely to recidivate. All of these things indicate serious violations of the assumptions underlying logistic regression here as with Konopasek’s (2011) initial model (Allison, 1999). As with the Cook et al. (2014) study, all of these issues mean that nothing presented in Konopasek (2011) is of any direct value in assessing the relationship between disclosure and recidivism. It is simply not rigorous research needed to assess the utility of post-conviction polygraph testing of sex offenders. ⁷

Conclusion

Similarly to what I stated above, I take no pleasure in writing articles that point out significant flaws in research. In addition, my criticisms here rest solely on the quality of the research and not on my position as a skeptic of post-conviction polygraph testing as I would lambaste any research containing these issues. I firmly believe that all of us engaged in this research seek the same result—how to punish, treat, and rehabilitate sexual offenders in the most humane but theoretically sound manner supported by reliable and replicable research that helps offenders and prevents further victimization. Indeed, rather than dismissing any future research that does not conform to my present position, I would wholeheartedly endorse the use of polygraphy in sex offender treatment if it could be shown with solid, replicated evidence that it worked well in reducing recidivism. Sadly, the current state of research in post-conviction polygraph testing does not have any decent, sound empirical support beyond that (a) it gets offenders to disclose ⁸ larger criminal careers and more varied sexual histories, and (b) offenders, clinicians, and correctional staff like it and think that it works. I will state this in no uncertain terms: We can take these two findings as facts, so we do not need more research into either of those areas. Instead, we desperately need well-designed research that evaluates polygraphy in sex offender treatment the same way we do with cognitive behavior therapy or other correctional interventions. One only needs to look at what is done with these other programs to see that it can be done and done well (MacKenzie, 2006).

In the spirit of Rosky (2013), I include suggestions here that proponents of post-conviction polygraph testing should take heed of to help them perform better research as they further investigate the procedure. The first is that proponents should seek out assistance from professional statisticians, preferably before proponents collect data, so that strong, experimental designs can be utilized, but also with analysis of secondary data from nonrandom sources. There are a plethora of analytic methods that can be used in a quasi-experimental design that statisticians utilize with this type of data, which would enhance the use of secondary data as evidence including the need for adequate comparison groups. The second is that they need to incorporate known correlates of crime with good construct validity and reliability, so that we can ascertain polygraphy testing’s utility as a correctional intervention with the least amount of confounding possible. The third is that while subjective perceptions of utility might assist with better treatment outcomes, we need to measure that behavioral change, so capture that information. Fourth, be more self-critical. If you indentify and discuss your research limitations in great detail, it will obviate the need for commentaries like this one. Fifth, and finally, stress uncertainty and variation rather than making black-and-white statements from nonrandom data that are not generalizable. These black-and-white statements merely add to the noise surrounding the polygraph testing of sex offenders rather than helping extract information.

In sum, the numerous statistical and research issues that I catalog from Jensen et al. (2015) along with similar but more extensive problems from both Cook et al. (2014) and Konopasek (2011) sufficiently demonstrate that these studies contain nothing new, viable, or believable that informs the debate regarding the use of polygraph in post-conviction sexual offender treatment. Quite simply, all of us, proponents and critics alike, need to do better jobs as researchers rather than continuously publishing the same criticisms or publishing more studies with small, nonrandom samples that leave themselves open to said criticisms. Again, we are all on the same side trying to help develop and evaluate treatment programs that reduce future criminality in a humane but scientifically supported manner. We all have to be ready to change our minds when good research speaks differently. I have been eagerly awaiting such research not just on polygraphy, but any correctional intervention. I hope that proponents are just as willing to change their minds as I am. In the meantime, I will continue to be an ardent skeptic of polygraph’s use in sex offender treatment and will continue to be critical of polygraphy research that is deeply flawed. I hope I am eventually proven wrong because if we critics are correct, it means that we wasted precious time and money and certainly created further victims using a meaningless tool. More importantly, we all, critics and proponents alike, will own these failures. The critics because we were unable to convince policy makers and clinicians not to use a deeply flawed tool and proponents for pushing widespread use of this flawed tool before it could be adequately evaluated.

Our task going forward is simple, and I hope that proponents will agree with me that we do not need agendas; we need either good research that supports polygraph testing’s utility as a tool that improves therapeutic outcomes that reduce criminality or such research that dismisses it so that we can move on to other more viable and humane correctional interventions that do work to reduce criminality. We owe this not only to the public wallet but also to the correctional staff who supervise and treat offenders; the offenders who are ready for change and those who can be changed; and, most importantly, future victims harmed from our easily preventable use of failed policies and ineffective correctional interventions.