Evaluation questions: Managing agency, bias and scale

It is common to see in the Terms of Reference (ToRs) of an evaluation a list of evaluation questions. Or, at least a requirement that the evaluator develops such a list of questions as part of the evaluation plan. Such questions are typically fairly open-ended “how” and “whether” type questions. On the surface this approach makes sense. It gives some focus but leaves room for the unexpected and unknown.

But perhaps there is an argument for a much more focused and pre-specified approach. 

Agency

There are two grounds on which such an argument could be made. One is that aid organisations implementing development programs have “agency”, i.e. they are expected to be able to assess the situation they are in and act on the basis of informed judgements. They are not just mechanical instruments for implementing a program, like a computer. Given this fact, one could argue that evaluations should not simply focus on the behaviour of an organisation and its consequences, but on the organisation’s knowledge of its behaviour and its consequences. If that knowledge is misinformed then the sustainability of any achievements may be seriously in doubt. Likewise, it may be less likely that unintended negative consequences of a program will be identified and responded to appropriately.

One way to assess an organisation’s knowledge is to solicit their judgements about program outcomes in a form that can be tested by independent observation. For example, an organisation’s view on the percentage of households who have been lifted above the poverty line as a result of a livelihood intervention. An external evaluation could then gather independent data to test this judgement, or more realistically, audit the quality of the data and analysis that the organisation used to come to their judgement. In this latter case the role of the external evaluator is undertake a meta-evaluation, evaluating an organisation’s capacity by examining their judgements relating to key areas of expected program performance. This would require focused evaluation questions rather than open ended evaluation questions.

Bias

The second argument is arises from a body of research and argument about the prevalence of what appears to be endemic bias in many fields of research: the under-reporting of negative findings (i.e. non-relationships) and the related tendency of positive findings to disappear over time. The evidence here makes salutary reading, especially the evidence from the field of medical research where research protocols are perhaps the most demanding of all (for good reason, given the stakes involved). Lehrer’s 2010 article in the New York Times “The Truth Wears Off: Is there something wrong with the scientific method?’ is a good introduction, and Ioannidis’ work (cited by Lehrer) provides the more in-depth analysis and evidence. 

One solution that has been proposed to the problem of under-reporting of negative findings is the establishment of trial registries, whereby plans for experiments would be lodged in advance, before their results are known. This is now established practice in some fields of research and has recently been proposed for the use of randomised control trials by development agencies[1] Trial registries can provide two lines of defence against bias. The first is to make visible all trials, regardless of whether they are deemed “successful” and get published, or not. The other defence is against inappropriate “data mining”[2] within individual trials. The risk is that researchers can examine so many possible correlations between independent and dependent variables that some positive correlations will appear by chance alone. This risk is greater where a study looks at more than one outcome measure and at several different sub-groups. Multiple outcome measures are likely to be used when examining the impact on complex phenomenon such a poverty levels or governance, for example. When there are many relationships being examined there is also the well known risk of publication bias, of the evaluator only reporting the significant results.

These risks can be managed partly by the researchers themselves. Rasmussen et al suggests that if the outcomes are assumed to be fully independent, statistical significance values should be divided by the number of tests. Other approaches involve constructing mean standardised outcomes across a family of outcome measures. However these do not deal with the problem of selective reporting of results. Rasmussen et al argue that this risk would be best dealt with through the use of trial registries, where relationships to be examined are recorded in advance. In other words, researchers would spell out the hypothesis or claim to be tested, rather than simply state an open ended question. Open ended questions invite cherry picking of results according to the researcher’s interests, especially when there are lot of them.

As I have noted elsewhere, there are risks with this approach. One concern is that it might prevent evaluators from looking at the data and identifying new hypothesis that genuinely emerges as being of interest and worth testing.  However, registering hypotheses to be tested would not preclude this possibility. It should, however, make it evident when this is happening, and therefore encourage the evaluator to provide an explicit rationale for why additional hypotheses are being tested.

Same again, on a larger scale

The problems of biased reporting re-appear when individual studies are aggregated. Ben Goldacre explains:  

“But individual experiments are not the end of the story. There is a second, crucial process in science, which is synthesising that evidence together to create a coherent picture.

In the very recent past, this was done badly. In the 1980s, researchers such as Celia Mulrow produced damning research showing that review articles in academic journals and textbooks, which everyone had trusted, actually presented a distorted and unrepresentative view, when compared with a systematic search of the academic literature. After struggling to exclude bias from every individual study, doctors and academics would then synthesise that evidence together with frightening arbitrariness.

The science of "systematic reviews" that grew from this research is exactly that: a science. It's a series of reproducible methods for searching information, to ensure that your evidence synthesis is as free from bias as your individual experiments. You describe not just what you found, but how you looked, which research databases you used, what search terms you typed, and so on. This apparently obvious manoeuvre has revolutionised the science of medicine”

Reviews face the same risks as individual experiments and evaluations. They may be selectively published, and their individual methodologies may not adequately deal with the problem of selective reporting of the more interesting results – sometimes described as cherry picking.  The development of review protocols and the registering of those prior to a review are an important means of reducing biased reporting, as they are with individual experiments. Systematic reviews are already a well established practice in the health sphere under the Cochrane Collaboration and in social policy under the Campbell Collaboration. Recently a new health sector journal, Systematic Reviews, has been established with the aim of ensuring that the results of all well-conducted systematic reviews are published, regardless of their outcome. The journal also aims to promote discussion of review methodologies, with the current issue including a paper on “Evidence summaries”, a rapid review approach.

It is common place for large aid organisations to request synthesis studies of achievements across a range of programs, defined by geography (e.g. a country program) or subject matter (e.g. livelihood interventions). A synthesis study requires some meta-evaluation, of what evidence is of sufficient quality and what is not. These judgements inform both the sampling of sources and the weighing of evidence found within the selected sources.  Despite the prevalence of synthesis studies, I am not aware of much literature existing on appropriate methodologies for such reviews, at least within the sphere of development evaluation. [I would welcome corrections to this view]

However, there are signs that experiences elsewhere with systematic reviews are being attended to. In the development field The International Development Coordinating Group has been established, under the auspices of the Campbell Collaboration, with the aim of encouraging registration of review plans and protocols and then disseminating “systematic reviews of high policy-relevance with a dedicated focus on social and economic development interventions in low and middle income countries”. DFID and AusAID have funded 3ie to commission a body of systematic reviews of what it identifies as rigorous impact evaluations, in a range of development fields. More recently an ODI Discussion Paper has reviewed some experiences with the implementation of systematic reviews. Associated with the publication of this paper was a useful online discussion.  

Three problems that were identified are of interest here. One is the difficulty of accessing source materials, especially evaluation reports many of which are not in the public domain, but should be. This problem is faced by all review methods, systematic and otherwise. This problem is now being addressed on multiple fronts, by individual organisation initiatives (e.g. 3ie and IDS evaluation databases) and by collective efforts such as the International Aid Transparency Initiative. The authors of the ODI paper note that “there are no guarantees that systematic reviews, or rather the individuals conducting them, will successfully identify every relevant study, meaning that subsequent conclusions may only partially reflect the true evidence base.” While this is (for any type of review process) it is the transparency of the sample selection - via protocols, and the visibility of the review itself – via registries, which help make this problem manageable.

The second problem, as seen by the authors, is that “Systematic reviews tend to privilege one kind of method over another, with full-blown randomised controlled trials (RCTs) often representing the ‘gold standard’ of methodology and in-depth qualitative evidence not really given the credit it deserves.” This does not have to be the case.   A systematic review has been usefully defined as “an overview of primary studies which contains an explicit statement of objectives, materials, and methods and has been conducted according to explicit and reproducible methodology” Replicability is key and this requires systematic and transparent process relating to sampling and analysis. This should be evident in protocols.

A third problem was identified by 3ie, in their commentary on the Discussion Paper. This relates directly to the initial focus of this blog, the argument for more focused evaluation questions. They comment that:

“Even with plenty of data available, making systematic reviews work for international development requires applying the methodology to clearly defined research questions on issues where a review seems sensible. This is one of the key lessons to emerge from recent applications of the methodology. A review in medicine will often ask a narrow question such as the Cochrane Collaboration’s recent review on the inefficacy of oseltamivir (tamiflu) for preventing and treating influenza. Many of the review questions development researchers have attempted to answer in recent systematic reviews seem too broad, which inevitably leads to challenges. There is a trade-off between depth and breath, but if our goal is to build a sustainable community of practice around credible, high quality reviews we should be favouring depth of analysis where a trade-off needs to be made.”

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[1] By the head of DFID EvD in 2011 and by Rasmussen et al, see below.

[2] See Ole Dahl Rasmussen, Nikolaj Malchow-Møller, Thomas Barnebeck Andersen, Walking the talk: the need for a trial registry for development interventions,  available via http://mande.co.uk/2011/uncategorized/walking-the-talk-the-need-for-a-trial-registry-for-development-interventions/

Evaluation quality standards: Theories in need of testing?

Since the beginning of this year I have been part of a DFID funded exercise which has the aim of “Developing a broader range of rigorous designs and methods for impact evaluations” Part of the brief has been to develop draft quality standards, to help identify “the difference between appropriate, high quality use of the approach and inappropriate/ poor quality use”

A quick search of what already exists suggests that there is no shortage of quality standards. Those relevant to development projects have been listed online here. They include:

• Standards agreed by multiple organisations, e.g. OECD-DAC and various national evaluation societies. The former are of interest to aid organisations where as the latter are of more interest to evaluators.
• Standards developed for use within individual organisations, e.g. DFID and EuropeAID
• Methodology specific standards, e.g. those relating to randomised and other kinds of experimental methods, and qualitative research

In addition there is a much larger body of academic literature on the use and mis-use of various more specific methods.

A scan of the criteria I have listed shows that a variety of types of evaluation criteria are used, including:

• Process criteria, where the focus is on how evaluations are done. e.g. relevance, timeliness, accessibility, inclusiveness
• Normative criteria, where the focus is on principles of behaviour e.g. independence, impartiality, ethicality
• Technical criteria, where the focus is on attributes of the methods used e.g. reliability and validity

Somewhat surprisingly, technical criteria like reliability and validity are in the minority, being two of at least 20 OECD-DAC criteria. The more encompassing topic of Evaluation Design is only one of the 17 main topics in the DFID Quality Assurance template for revising draft evaluations. There are three possible reasons why this is so: (a) Process attributes may be more important, in terms of their effects on what happens to an evaluation, during and after its production, (b) It is hard to identify generic quality criteria for a diversity of evaluation methodologies, (c) Lists have no size limits. For example, the DFID QA template has 85 subsidiary questions under 17 main topics.

Given these circumstances what is the best way forward, of addressing the need for quality standards for “a broader range of rigorous designs and methods for impact evaluations”? The first step might be to develop specific guidance which can be packed in separate notes on particular evaluation designs and methods. The primary problem may be simple lack of knowledge about the methods available; knowing how to choose between them may be in fact “a problem we would like to have”, which needs to be addressed after people at least know something about the alternative methods. The Asian Development Bank has addressed this issue through its “Knowledge Solutions” series of publications. 

The second step that could be taken would be to develop more generic guidance that can be incorporated into the existing quality standards. Our initial proposal focused on developing some additional design focused quality standards that could be used with some reliability across different users. But perhaps this is a side issue. Finding out what quality criteria really matter, may be more important. However, there seems to be very little evidence on what quality attributes matter. In 2008 Forss et al carried out a study: “Are Sida Evaluations Good Enough? An Assessment of 34 Evaluation Reports” The authors gathered and analysed empirical data on 40 different quality attributes of evaluation reports published between 2003 and 2005. Despite suggestions made, the report was not required to examine the relationship between these attributes and the subsequent use of the evaluations. Yet, the insufficient use of evaluations has been a long standing concern to evaluators and to those funding evaluations. 

There are at least 4 different hypotheses that would be worth testing in future versions of the SIDA study that did look at evaluation quality and usage:

1. Quality is largely irrelevant, what matters is how the evaluation results are communicated.
2. Quality matters, especially the use of a rigorous methodology, which is able to address attribution issues
3. Quality matters, especially the use of participatory processes that engage stakeholders
4. Quality matters, but it is a multi-dimensional issue. The more dimensions are addressed, the more likely that the evaluation results will be used.

The first is in effect the null hypothesis, and one which needs to be taken seriously. The second hypothesis seems to be the position taken by 3ie and other advocates of RCTs and their next-best substitutes. It could be described as the killer assumption being made by RCT advocates that is yet to be tested. The third could be the position of some of the supporters of the “Big Push Back” against inappropriate demands for performance reporting. The fourth is the view present in the OECD-DAC evaluation standards, which can be read as a narrative theory of change about how a complex of evaluation quality features will lead to evaluation use, strengthened accountability, contribute to learning and improved development outcomes. I have taken the liberty of identifying the various possible causal connections in that theory of change in this network diagram below. As noted above, one interesting feature is that the attributes of reliability and validity are only one part of a much bigger picture. 

[Click on image to view a larger version of the diagram]

While we wait for the evidence…

We should consider transparency as a pre-eminent quality criterion, which would be applicable across all types of evaluation designs. It is a meta-quality, enabling judgments about other qualities. It also addresses the issue of robustness, which was of concern to DFID. The more explicit and articulated an evaluation design is, the more vulnerable it will be to criticism and identification of error. Robust designs will be those that  can survive this process. This view connects to wider ideas in the philosophy of science about the importance of falsifiablity as a quality of scientific theories (promoted by Popper and others).

Transparency might be expected at both a macro and micro level. At the macro level, we might ask these types of quality assurance questions:

• Before the evaluation: Has an evaluation plan been lodged, which includes the hypotheses to be tested? Doing so will help reduce selective reporting and opportunistic data mining
• After the evaluation: Is the evaluation report available? Is the raw data available for re-analysis using the same or different methods?

Substantial progress is now being made with the availability of evaluation reports. Some bilateral agencies are considering the use of evaluation/trial registries, which are increasingly commonplace in some field of research. However, availability of raw data seems likely to remain the most challenging requirement for many evaluators.

At the micro-level, more transparency could be expected in the particular contents of evaluation plans and reports. The DFID Quality Assurance templates seem to be most operationalised set of evaluation quality standards available at present. The following types of questions could be considered for inclusion in those templates:

• Is it clear how specific features of the project/program influenced the evaluation design?
• Have rejected evaluation design choices been explained?
• Have terms like impact been clearly defined?
• What kinds of impact were examined?
• Where attribution is claimed is there also a plausible explanations of the causal processes at work?
• Have distinctions been made between causes which are necessary, sufficient or neither (but still contributory)?
•  Are there assessments of what would have happened without the intervention?

This approach seems to have some support in other spheres of evaluation work, not associated with development aid: “The transparency, or clarity, in the reporting of individual studies is key” TREND statement, 2004

In summary, three main recommendations have been made above:

• Develop technical guidance notes, separate from additional quality criteria
• Identify specific areas where transparency of evaluation designs and methods is essential, for possible inclusion in DFID QA templates, and the like
• Seek and use opportunities to test out the relevance of different evaluation criteria, in terms of  their effects on evaluation use

PS: This text was the basis of one of the presentations to DFID staff (and others) in a workshop on 7^th October 2011 on the subject of “Developing a broader range of rigorous designs and methods for impact evaluations” The views expressed above are my own and should not be taken to reflect the views of either DFID or others involved in the exercise.

Relative rather than absolute counterfactuals: A more useful alternative?

Background

The basic design of a randomised control trial (RCT) involves comparisons of two groups: an intervention (or “treatment”) group and a control group, at two points of time, before an intervention begins and after the intervention ends. The expectation (hypothesis) is that there will be a bigger change on an agreed impact measure in the intervention group than in the control group. This hypothesis can be tested by comparing the average change in the impact status of members of the two groups, and applying a statistical test to establish that this difference was unlikely to be a chance finding (e.g. less than 5% probability of being a chance difference). The two groups are made comparable by randomly assigning participants to both groups. The types of comparisons involved are shown in this fictional example below.

	A.       Intervention group	B.       Control group
Before intervention	Average income per household = $1000 year. N = 500	Average income per household = $1000 year N=500
After intervention	Average income per household = $1500 year. N = 500	Average income per household = $1200 year N=500
PS: See Comment 3 below re this table]	Difference over time = $500	Difference over time = $200
	Difference between changes in A and B = £300

This method allows a comparison with what could be called an absolute counterfactual: what would have happened if there was no intervention.

Note that only the impact indicator is measured, there is no measurement of the intervention. This is because the intervention is assumed to be the same across all participants in the intervention group. This assumption is reasonable with some development interventions, such as those involving financial or medical activities (e.g. cash transfers or de-worming). Some information based interventions, using radio programs or the distribution of booklets, can also be assumed to be available to all participants in a standardised form. Where delivery is standardised it makes sense to measure the average impacts on the intervention and control group, because significant variations in impact are not expected to arise from the intervention.

Alternate views

There are however many development interventions where delivery is not expected to be standardised and where the opposite is the case, that delivery is expected to be customised. Here the agent delivering the intervention is expected to have some autonomy and to use that autonomy to the benefit of the participants. Examples of such agents would include community development workers, agricultural extension workers, teachers, nurses, midwives, nurses, doctors, plus all their supervisors. On a more collective level would be providers of training to such groups working in different locations. Also included would be almost all forms of technical assistance provided by development agencies.

In these settings measurement of the intervention, as well as the actual impact, will be essential before any conclusions can be drawn about attribution – the extent to which the intervention caused the observed impacts. Let us temporarily assume that it will be possible to come up with a measurement of the degree to which an intervention has been successfully implemented, a quality measure of some kind. It might be very crude, such as number of days an extension worker has spent in villages they are responsible for, or it might be a more sophisticated index combining multiple attributes of quality (e.g. weighted checklists).

Data on implementation quality and observed impact (i.e. an After minus a Before measure) can now be brought together in a two dimensional scatter plot. In this exercise there is no longer a control group, just an intervention group where implementation has been variable but measured. This provides an opportunity to explore the relative counterfactual, what would have happened if implementation was less successful, and less successful still, etc. In this situation we could hypothesise that if the intervention did cause the observed impacts then there would be a statistically significant correlation between the quality of implementation and observed impact. In place of an absolute counterfactual obtained via the use of control group, where there was no intervention we have relative counterfactuals, in the form of participants exposed to interventions of different qualities. In place of an average, we have a correlation.

There are a number of advantages to this approach. Firstly, with the same amount of evaluation funds available, the number of intervention cases that can be measured can be doubled, because a control group is no longer being used. In addition to obtaining (or not) a statistically significant correlation, we can also identify the strength of the relationship between the intervention and the impact. This will be visible in the slope of the regression line. A steep slope[1] would imply that small improvements in implementation can make big improvements in observed impacts and vice versa. If a non-lineal relationship is found then the shape of a best fitting regression line might also be informative, about where improvements will generate more versus less improvement.

Another typical feature of scatter plots is outliers. There may be some participants (individuals or groups of) who have received a high quality intervention, but where the impact has been modest, i.e. a negative outlier. Conversely, there may be some participants who have received a poor quality intervention, but where the impact has been impressive, i.e. a positive outlier. These are both important learning opportunities, which could be explored via the use of in-depth cases studies . But ideally these case studies would be informed by some theory, directing us where to look.

Evaluators sometimes talk about implementation failure versus theory failure. In her Genuine Evaluation blogPatricia Rogers gives an interesting example from Ghana, involving the distribution of Vitamin A tablets to women in order to reduce pregnancy related mortality rates. Contrary to previous findings, there was no significant impact. But as Patricia noted, the researchers appeared to have failed to measure compliance i.e. whether all the women actually took the tables given to them! This appears to be a serious case of implementation failure, in that the implementers could have designed a delivery mechanism that ensured compliance. Theory failure would be where our understanding of how Vitamin A affects women’s health appears to be faulty, because expected impacts do not materialise, after women have taken the prescribed medication.

In the argument developed so far, we have already proposed measuring quality of implementation, rather than making any assumptions about how it is happening. However, it is still possible that we might face “implementation measurement failure”. In other words, there may be some aspect of the implementation process that was not captured by the measure used, and which was causally connected to the conspicuous impact, or lack thereof.  A case study, looking at the implementation process in the outlier cases might help us identify the missing dimension. Re-measurement of implementation success incorporating this dimension might produce a higher correlation result. If it did not, then we might by default then have a good reason to believe we are now dealing with theory failure, i.e. a lack of understanding of how an intervention has its impact. Again, case studies of the outliers could help generate hypotheses about these. Testing these out is likely to be more expensive than testing alternate views on implementation processes because data will be less readily at hand. For reasons of economy and practicality implementation failure should be our first suspect.

In addition to having informative outliers to explore, the use of a scatter plot enables us to identify another potential outcome not readily available via the use of control groups, where the focus is on averages. In some programmes poor implementation may not simply lead to no impact (i.e. no difference between the average impact of control and intervention groups). Poor implementation may lead to negative impacts. For example, a poorly managed savings and credit programme may lead to increased indebtedness in some communities. In a standard comparison between intervention and control groups this type of failure would usually need to be present in a large of cases before it became visible in a net negative average impact. In a scatter plot any negative cases would be immediately visible, including their relationship to implementation quality.

To summarise so far, the assumption about standardised delivery of an intervention does not fit the reality of many development programmes. Replacing assumptions by measurement will provide a much richer picture of the relationship between an intervention and the expected impacts. Overall impact can still be measured, by using a correlation coefficient. In addition we can see the potential for greater impact present in existing implementation practice (the slope of the regression line). We can also find outliers that can help improve our understanding of implementation and impact process. We can also quickly identify negative impacts, as well as the absence of any impact.

Perhaps more important still, the exploration of internal differences in implementation means that the autonomy of development agents can be valued and encouraged. Local experimentation might then generate more useful outliers, and not be seen simply as statistical noise. This is experimentation with a small e, of the kind advocated by Chris Blattman in his presentationto DFID on 1^st September 2011, and of a kind long advocated by most competent NGOs.

Given this discussion is about counterfactuals, it might be worth considering what would happen if this implementation measurement based approach was not used, where an intervention is being delivered in a non-standard way. One example is a quasi-experimental evaluation of an agricultural project in Tanzania, described in Oxfam GB‘s paper on its Global Performance Framework[2] . “Oxfam is working with local partners in four districts of Shinyanga Region, Tanzania, to support over 4,000 smallholder  farmers (54% of whom are women) to enhance their production and marketing of local chicken and rice. To promote group cohesion and solidarity, the producers are encouraged to form themselves into savings and internal lending communities. They are also provided with specialised training and marketing supporting, including forming linkages with buyers through the establishment of collection centres.” This is a classic case where the staff of the partner organisations would need to exercise considerable judgement about how to best help each community. It is unlikely that each community was given a standard package of assistance, without any deliberate customisations nor any unintentional quality variations along the way. Nevertheless, the evaluation chose to measure the impact of the partner’s activities on changes in household incomes and women’s decision making power, by comparing the intervention group with a control group. Results of the two groups were described in terms of “% of targeted households living on more than £1.00 per day per capita”, and % of supported women are meaningfully involved in household decision making”. In using these measures to make comparisons Oxfam GB has effectively treated quality differences in the extension work as noise to be ignored, rather than as valuable information to be analysed. In the process they have unintentionally devalued the work of their partners.

A similar problem can be found elsewhere in the same document where Oxfam GB describes their new set of global outcome indicators. The Livelihood Support indicator is: % of targeted households living on more than £1.00 per day per capita (as used in the Tanzania example). In four of the six global indicators the unit of analysis are people, the ultimate intended beneficiaries of Oxfam GB’s work. However, the problem is that in most cases Oxfam GB does not work directly with such people. Instead Oxfam GB typically works with local NGOs who in turn work with such groups. In claiming to have increased the % of targeted households living on more than £1.00 per day per capita Oxfam GB is again obscuring through simplification the fact that it is those partners who are responsible for these achievements. Instead, I would argue that the unit of analysis many of Oxfam GB’s global outcome indicators should be the behaviour and performance of its partners. Its global indicator for Livelihood Support should read something like this: “x % of Oxfam GB partners working on rural livelihoods have managed to double the proportion of targeted households living on more than £1.00 per day per capita” Credit should be given to where credit is due.  However, these kinds of claims will only be possible if and where Oxfam GB encourages partners to measure their implementation performance as well as changes taking place in the communities they are working with, and then to analyse the relationship between both measures.

Ironically, the suggestion to measure implementation sounds rather unfashionable and regressive, because we are often reading how in the past aid organisations used to focus too much on outputs and that now they need to focus more on impacts. But in practice it is not an either/or question. What we need is both, and both done well. Not something quickly produced by the Department of Rough Measures.

PS 4th September 2011: I forgot to discuss the issue of whether any form of randomisation would be useful where relative counterfactuals are being explored. In an absolute counterfactual experiment the recipients’ membership of control versus intervention groups is randomised. In a relative counterfactual “experiment” all participants will receive an intervention so there is no need to randomly assign participants to control versus intervention groups. But randomisation could be used to decide which staff worked with which participants (/vice versa). For example, where a single extension worker is assigned to a given community. But this would be less easily where a whole group of staff e.g. in a local health centre or local school, are responsible for the surrounding community.

Even where randomisation of staff was possible this would not prevent the impact of external factors influencing the impact of the intervention. It could be argued that the groups experiencing least impact and the poorest quality implementation were doing so, because of the influence of an independent cause (e.g. geographical isolation) that is not present amongst the groups experiencing bigger impacts and better quality implementation. Geographical isolation is a common exterbal influence in many rural development projects, one which is likely to make implementation of a livelihood initiative more difficult as well as making it more difficult for the participants to realise any benefits e.g. through sales of new produce at a regional market. Other external influences may affect the impact but not the intervention e.g. subsequent changes in market prices for produce. However, identifying the significance of external influences should be relatively easy, by making statistical tests of the difference in their prevalence in the high and low impact groups. This does of course require being able to identify potential external influences whereas as with randomised control trials (RCTs) no knowledge of other possible causes is needed (their influence is assumed to be equally distributed between control and intervention groups). However, this requirement could be considered as a "feature" rather than a "bug", because exploration of the role of other causal factors could inform and help improve implementation. On the other hand, the randomisation of control and intervention groups could encourage management's neglect of the role of other causal factors. There are clearly trade-offs here between competing evaluation quality criteria of rigour and utility.

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[1]i.e. with observed impact on the y axis and intervention quality on the x axis

[2]Can we obtain the required rigour without randomisation? Oxfam GB’s non-experimental
Global Performance Framework. Karl Hughes, Claire Hutchings. August 2011

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