Where to next in corruption research?

nine half-baked observations/ideas

Dieter Zinnbauer
15 min readMar 8, 2018

*I wrote this essay in late 2017 as a contribution to the Expert Network on Rethinking Corruption kindly convened by The British Academy-Department for International Development Anti-Corruption Evidence (ACE) Programme. It is deliberately written in a somewhat speculative and provocative tone in order to inspire a good debate on these issues. All views are strictly mine.

In a nutshell

A re-fresh of anti-corruption research is in my view not so much about chasing new topics, but about re-jigging some implicit assumptions and re-thinking some standard approaches to how corruption research is currently being funded, designed, organised and consumed. With regard to general assumptions, accepting the centrality of power, recognizing the need to embed more –often in a secondary role — into broader research programmes and sectoral communities and dialing-down expectations about what anti-corruption research can realistically deliver would go a long way to help such a refresh. This would build the basis for revisiting the main approaches and ways corruption research is being organised. Very useful in this area would be research approaches that are more plural and open-ended, research formats and funding schemes that are more patient and inform a fuller understanding of corruption in broader social, economic and political contexts and that at the other end of the spectrum would also enable collaborations that are more attuned to rapid policy-learning and securing the long-term data foundations in the field. With regard to promising research topics I simply offer by way of example some of my personal favourites of what could be a very long and very subjective laundry list.

In essence, I argue for a cheerful embrace of a sense of anti-parsimoniousness and possibilism. The former is Haidt’s plea to let go of easy explanations, embrace thick descriptions and the creative clash of valid, yet seemingly incompatible explanations as the most promising strategies to better come to grips with the messiness of human and organisational behaviour.[1] The later refers to Hirschman’s call for putting aside the explanatory cookie-cutter and adopt an “approach to the social world that would stress the unique rather than the general, the unexpected rather than the expected, and the possible rather than the probable.”[2]

Nine suggestions for a refresh of corruption research

The following are some admittedly very subjective thoughts, some of them phrased in rather provocative terms but all offered in good-faith to inspire a robust, productive discussion. I organise these notes loosely in three broad “containers” of overlooked/underutilized/fresh

  • assumptions that, if accepted, would suggest changes in research funding, designs and user expectations;
  • approaches that partly flow from these assumptions and offer some ideas for the actual organisation of research and the types of questions to asked and methods to deploy; and,
  • issues/topics that seem promising to focus more on.

The third container will be a rather small one, since I believe that future-proofing corruption research is not such much about identifying new topics as it is about re-thinking some of the underlying assumptions and the actual ways research is being organised, which would then organically surface new and overlooked issues and topics worth investigating.

A General assumptions and observations

1 Lip-service to the centrality of power — but not reflected in research designs

Anti-corruption is not a promote hand-washing type of intervention. It is essentially and ultimately about power. This is by now a widely-invoked perspective but it has in my view not really informed research designs and funding in sufficient ways beyond a bolted-on, rather general appeal to think politically in intervention design. At the end of the day, AC research still too much builds on implicit conceptual templates from natural sciences or technocratic development interventions (i.e. the classic hand-washing problem to boost hygiene standards) neither of which have power and power relations as a constitutive part of the problem to tackle. We are not in search of a vaccine against corruption, to be deployed in fail-safe ways around the world to eradicate the disease of irresponsible government conduct. Tackling corruption by definition rubs against vested interests and powers. It is about supporting an age-old, continuous struggle for more social justice at particular inflection points. Some privileged players will almost inevitably loose. As a consequence, outright push-back, inventive resistance and shrewd sabotage are to be expected as the norm, rather than as an outlier or occasional side effect. And the forms and efficacy of such a push-back are likely to fully unfold over a longer term, cannot be anticipated and thus require adaptive, sustained responses. As a consequence, anti-corruption interventions may have a performance footprint that is very often altered, or even annulled in the longer-run and at best a jumpy roller-coaster with an upward tendency rather than a straight ladder towards more accountability.[3] All this however is insufficiently reflected in research designs that focus on short-term, fairly immediate (non)impacts, as well as on a narrow set of involved and impacted players (e.g. the hospital patient, the police) rather than the broader surroundings that might be more consequential for longer-term, deeper possibilities of change. And it gives rise to donor ambitions that expect rather clear impact footprints for anti-corruption interventions and related research designs. As a consequence, very few studies seek to follow interventions over a longer-term and very few keep an open mind for capturing unintended impacts and strange ripple effects that might open surprising possibilities for transformation change. Instead they risk to end up suggesting a narrow set of proven interventions that might actually be rather ineffective in the longer run and in other settings.

2 We cannot tackle or even fully understand corruption by just researching corruption

This builds on Danny Kaufman’s dictum that often one cannot fight corruption by fighting corruption. I think this also applies to corruption research. Arguably, most improvements in governance and integrity have been by-products of other reforms, political opportunism or sectoral transformations through new business models or technologies. All these dynamics and the mechanisms with which they influence corruption are taking place outside the narrow confines of corruption dynamics proper. They are difficult to appreciate and capture by research that focusses almost exclusively on one thin slice of this reality called corruption.

Corruption research has made some progress in going interdisciplinary, yet could hugely benefit by cooperating more outside the broader governance community. Knowing corruption may be somewhat adequate for scaling the outline of the problem, but it is most likely not enough for fully understanding the phenomenon in its actual manifestations and almost certainly insufficient for envisioning, trying out and learning from a much broader set of possible responses and change dynamics. Very few corruption researchers collaborate with sectoral experts — with actual health researchers, urbanists, or logistics experts when examining and experimenting around tackling corruption in healthcare, cities or customs situations. Both corruption research and practice could do much more to foster such collaborations.

In my view the most promising corruption research of the future might have to embed itself and actually accept a secondary, more strategic-supplemental, rather than central role in broader research efforts around improving health, education, economic or other human development outcomes. To put it bluntly: corruption is a difficult, perhaps even unhelpful prism and conceptual anchor for researching most related phenomena.

3 Lowering expectations will create fresh momentum

Policy-oriented corruption research seems to be somewhat bogged down by unrealistic expectations in the broader community of what it can realistically deliver.

No big data dive, systematic literature review, or even the most sophisticated Metaketa roll-out of RCTs will be able to authoritatively settle the question of what works-what does not in anti-corruption with a reasonable confidence in broader applicability and validity over time. Here are three reasons (many more could be added) why I think this is the case:

  • the imprecision of, huge inherent variance in and risk of over-interpreting a lot of quantitative corruption research that builds on aggregating a small set of what are often highly subjective, ambiguous, ordinal-scale survey questions and regresses them onto a set of equally amorphous variables in a rather small-N set of countries or contexts;
  • the limited external validity of even the most sophisticated RCTs and the extreme contingency, context-specificity and time-boundedness of anti-corruption interventions more generally; and,
  • the expected push-back and/or longer-term adaptation and counter strategies by corrupt powers to be curbed, all reactions that transcend narrow, time-bound research inquiries (see A above).

Against this backdrop, a more realistic set of policy-oriented ambitions for anti-corruption research would be to:

  • deliver at a maximum a reasonable proof of concept that something could in principal be promising; and/ or,
  • offer a sound view on whether some very specific initiative (much more specific than e.g. “transparency”) is achieving something very specific (much more specific than “tackling corruption”) in a given place and time period; and/or,
  • broaden the imagination of anti-corruption reformers re. the range of dynamics at play and levers at hand, by going deeper and broader (see B1), working inductively from positive outliers and branching out into partnerships with sectoral and other experts.

Rejigging such expectations may in the short run dampen the enthusiasm of research donors and research users. Yet, it will ultimately help avoid inevitable deeper frustrations further down the road and pave the way for fresh, more open, creative and adaptive funding, research and action programmes.

B Research arrangements

The primary challenge for corruption research going forward is to find new modes of organising itself in ways that make it easier to go multi-perspective, interface directly with existing policy interventions and that also makes the available resources more stable and go further. Here in more detail why these three challenges are important and first thoughts on how to re-organise to address them.

4 Broader, deeper, longer — or — “when a fight breaks out, watch the crowd”[4]

Most research on anti-corruption quite understandably focuses on the actors involved, the actions carried out and the actual offices, companies or locations where it all happens. However, such a limited focus on where it is at and who is at it, fails to pick up on the weaker signals and ripples in the broader environment that might ultimately be much more consequential and interesting when assessing the promise or impact of a particular anti-corruption intervention.

It would thus be very interesting to:

  • broaden the scope of investigation to cast a wider net that include the by-standers, the ones that could, but do not partake, the ones that are indirectly affected, could indirectly help or obstruct;
  • weave in more open-ended ethnographic research in very targeted ways that could help get at unforeseen dynamics, surprising interpretative frames, looming inconsistencies and deeper motivations; and,
  • add research initiatives with much longer time-horizons capture some of the push-back and responses that are vital to more effective longer-term strategies.

This makes admittedly for a much more ambitious, plural, resource-intensive and messy research programme but it may help capture some of the ripple effects, indirect bottlenecks or potential levers for change that help re-prioritise action and develop a more educated guess about the future trajectory of corruption and anti-corruption efforts.

5 Urgently needed and eminently possible: new research collaboratives for the basic data fundaments of anti-corruption — before it all crumbles

There is a huge world out there of what are considered rather boring, pedestrian data collection exercises. They range from the myriad of corruption related surveys to diagnostic exercises that assess, score, compare, track, aggregate the transparency, accountability and integrity of anything from international organisations and multi-national companies, to national party financing to local governance systems. Most of these exercises area undertaken by non-profits and policy entrepreneurs, not academia. Not all of them are super-useful, but the better ones are arguably some of the most relevant research-to-policy exercises that shine an informed light on the status of integrity and corruption, establish highly effective peer pressure for change and in the research domain provide the vital raw data material that the bulk of academic corruption research builds on one way or another.

The research and policy value of these exercises critically depends on being reasonably up-to-date, on a continuous refinement of the diagnostics applied and on regular repeats of core segments that build-up precious times-series datasets. The problem is that most of these exercises are very labour and resource intensive. In times of impact-oriented funding and rapid-impact advocacy however, these exercises are increasingly difficult to sell, both inside think tanks and non-profits that carry them out and on the outside to potential donors. Many of these exercises are teetering on the brink of collapse, move to longer, at times irregular intervals, narrow their scope or have folded already. Academia is also loath to fill this gap since periodic, expensive data trawls are not exactly an easy ticket to publishing fame, fund-raising prowess and tenure.

Yet, academic researchers will have to jump in and contribute to these essential data-gathering exercises before it is too late. Fortunately, there are a plethora of new collaborative templates out there that could and urgently should be experimented with to make this happen. Can we envision some sort of scholarly crowd-funding or pooling of resources for the next round of corruption household survey x? Can we turn the much needed updates to an assessment of the asset disclosure regime in country y into an annual in-class exercise for a graduate class in political science under competent course supervision? Could we establish some sort of corruption assessment clinics borrowing from how law school use student/faculty resources to real world problems while at the same time giving their students hands-on experience?

Re-focussing attention on this basic data plumbing and devising new types of research collaboratives to safeguard their survival and continuing evolution will be an urgent task in corruption research for the years ahead.

6 Adaptive projects, adaptive research and rapid feed-back loops

There is growing momentum for moving policy interventions of all types into more agile territory by widening spaces for experimentation, giving preference to highly adaptable, designs over tightly log-framed, pre-programmed execution and by establishing much more rapid feedback loops to accelerate learning and adaptation. This shift in intervention thinking should be particularly relevant for anti-corruption work that is often highly volatile and vulnerable to push-backs. And the importance that this paradigm accords to rapid learning opens a very important role for corruption research.

The main challenge however will be how to devise research strategies and practically organise the research so that it can actually function as rapid feedback loop back into project adaptations and iterative experimentation. The much closer collaboration between research, policy implementers that this will have to be based on will require some compromising on all sides.

For project implementers, governments, multilaterals, as well as civil society, it will mean to buy into real learning, not polite consultants’ assessments, cede some message control and entertain the thought that some inconvenient insights may surface. For research it will require to forego the notion of the pure academic inquiry. It will mean to shift investments somewhat from lab- and research-driven field experiments into carefully crafting a research component onto existing practical projects and dynamics, prioritising the learning needs of the involved stakeholders over testing hypothesis born in the world of abstract theory.

For donors it will require to help convene conversations between research and practice early on to match up and integrate the two. And in very practical terms donors might also want to check whether the current funding arrangements, reporting requirements and impact expectations really align incentives for such alliances rather than deterring them.

There are some promising examples of such collaborations, e.g. Fix-my-street in the UK inviting in several research groups to work with its data, but much more could be done.

C Issues/topics for future research

Re-working assumptions and research arrangements is currently more important than digging up new topics, some of which will emerge organically from this re-organisation. Others candidates for newness might turn out to be not so unique after all, when digging deeper into the large trove of corruption-relevant research that has been assembled over decades, albeit at times under different labels and disciplinary domains. And in my view the big elephant in the room and unrivalled priority for corruption research that is focussing on industrialised countries are the moresubtle practices, unaligned incentives and adverse structural configurations that amount to phenomena such as policy, science or discourse capture and institutional corruption. Since it is contested however whether these issues qualify as corruption in a conventional sense I do not include them here. Nevertheless, here a handful of suggestions of what I would regard as very interesting topics for more research.

7 Technology and corruption: more back to basics and more forward into the future

There is a strong and very important focus in research and policy on teasing out the anti-corruption implications of social media and anything internet 2.0, often subsumed under the label of civic tech.

In contrast, what remains very much under-researched are a generation of more established new technologies, electronic government reform initiatives that are more mundane, but as I would argue potentially even more transformative and consequential for anti-corruption. Likewise, there is very little attention from a corruption research angle on the more emergent end of the technology spectrum around algorithms, internet of things and related applications that urgently need to be critically examined at a time when their architectures and usage arrangements are still very malleable.

E-government 1.0

Electronic government reform initiative that seek to streamline service delivery and internal organisation of administrations have been underway and are continuously expanding all around the world. Yet with some notable exceptions there is hardly any serious research done on how these reforms actually play out, how they affect corruption and anti-corruption. Example: I am not aware of any detailed accounts about whether the introduction of electronic case management systems in the judiciary system, which has taken place in many countries, has or has not had an impact upon the many corruption risks in this area.

Algorithms and corruption

The ethics and (lack of) accountability that comes with the deployment of ever more sophisticated and artificial-intelligence supported algorithms is a hot button issue at the moment. Yet, very little research looks at the upside and is deployed to probe the potential of algorithms to support ant-corruption work. For example, advanced matching algorithms are hoped to organise fair allocations of resources under extreme and extremely consequential scarcity, such as places at schools or organ donations, where corruption risks are extraordinarily high.

Internet of things (IoT), blockchain and satellite imaging

These areas are brimming with start-ups and enthusiastic media coverage as to their potential for tackling corruption, for example in supply chains (IoT), land governance (blockchain) or forest management (satellite imaging). Yet, beyond industry promotions and some policy reports no significant, deeper, critical analysis of any of these claims seem to be available. And looking at major working paper repositories and academic conference proceedings, almost no work on these issues seems to be in the pipeline either, although sound scholarly inquiries could be very timely to help inform the evolving designs of some of these technologies in ways that actually make them useful for tackling corruption.

8 Informal livelihoods and corruption

Informal economies and livelihoods play a central role in rural areas and fast-growing cities alike. Yet besides some macro-regressions and a very limited amount of work by ethnographers and geographers there is close to zero systematic and constructive research on the nexus between the two. To what extent and how are informal livelihoods impacted by corruption? What strategies of resistance, what outside interventions are possible that protect vital livelihoods, while disrupting the corruption rents that exploit and provide incentives to perpetuate the precarious nature of informal livelihoods? Such questions will help move the debate beyond a mere formalize-and-eradicate rhetoric that is very unhelpful and as to date still deters many important stakeholders and researches working on informality to engage with the anti-corruption agenda.

9 Debt, credit and corruption

A cursory look at the literature suggests that the corrupt control of central parts of the banking system and the ability to use capital and credit to cronies was a central concern of corruption research a couple of decades ago. Yet, despite the enormous importance of these mechanisms as engine for crony capitalism and rent-seeking this strand of research into corrupt subsidies and credit allocation via state-controlled banks, national development agencies, public investment funds or export credit institutions seems to have faded into the background, eclipsed perhaps a bit by a strong focus on procurement related corruption. The persistent importance of this mechanism, combined with the arrival of new players and new related financial products makes this a very promising area for research to revisit.

[1] Haidt, J. (2014): The pursuit of Parsimony, contributions for Edge.org: https://www.edge.org/response-detail/25346

[2] Hirschman, A. O. (1971) A Bias for Hope: Essays on Development and Latin America. New Haven, CT : Yale University Press

[3] For some related observations in the much-hyped area of nudging Sunstein introduced the concept of counter-nudges that are being devised by vested interests to blunt the effect of regulatory nudging. See Sunstein, Cass R., Nudges That Fail (July 18, 2016); working paper available at SSRN: https://ssrn.com/abstract=2809658

[4] Attributed to E. E. Schattschneider, quoted in Maisel, L. S., & Berry, J. M. (Eds.). (2010). The Oxford handbook of American political parties and interest groups. OUP Oxford.



Dieter Zinnbauer

governance, innovation, justice, tech and cities — copenhagen business school — views all mine