Last month we introduced the idea of a discounted Net Present Value calculation as one of the most effective ways to evaluate multiple opportunities. We pointed out that general business risk requires even the most certain of revenue streams to be discounted at around 10% to 15% before an investment of dollars today could balance the risk of the promise of future dollars. We also pointed out that this discount rate grows very rapidly where there are significant technical risks.
We summarized risks more or less as:
In general, the job of the Research Manager is to reduce risk and push down the level of discounting needed to justify the funding of projects. The Research Manager is usually working with questionable or unknown technologies and is trying to assess and improve the probability of success. The nature of the question may be completely open or quite narrow. The organization may have a problem for which there is no known or even suspected solution. Alternatively, the problem may have multiple solutions and the issue may be simply finding the best solution. To make matters more complex, the Research Manager often has a mix of projects ranging from Moderate Risk to Blue Sky and needs to assign resources in the most effective way.
Before we go any further we should discuss the “Aversion for Loss.” We have been talking about Risk in terms of assessing potential Gain. One thing that we must make clear is that Gain and Loss are not symmetrical in the human mind. We do not perceive the probability of Loss as simply 1 minus the probability of Gain. Even though this might be mathematically so, we do not perceive it that way, and for good reason. Failure is almost always punished more severely that success is rewarded – especially in the eyes of the one being punished or rewarded. We are all very averse to Loss and Failure – far more so that our desire for gain.
The Research Manager should always keep this in mind. No project will be funded by Executive Management that has a significant chance of destroying the Company. Very few projects will be funded by Executive Management that has a significant risk of being detrimental to the careers of the Executive Managers. Furthermore, no responsible Management Team would knowingly risk serious injury or loss of life. Hence, a significant part of the Research Manager’s success will be based on the ability to ferret out the consequences of a “failure” and make sure that those consequences are not catastrophic for the Company, Management, Employees, Owners or other Stakeholders. A catastrophic failure is one that can lead to all kinds of secondary consequential losses, among them destruction of property, loss of customer base or, heaven forbid, injury or loss of life.
Having said the above, it must be admitted that no project is without some risk and sometimes even unknown risk. A key to avoiding legal repercussions is using “reasonable care” and applying “professional judgement.” To avoid ethical issues one should seek to avoid Moral Hazard. In no case should others be unwittingly subjected to risks disproportionate to their potential gain. When there is doubt, full disclosure of the risks should be made to interested parties so that they may participate in balancing of risks and benefits from their perspective.
Now back to the Research Manager’s dilemma. In practice, the Research Manager quite often has a number of tasks to choose from. There’s the mundane library study on which brand of catalyst to buy and then there’s that “Blue Sky” project of developing the means to impress any desired catalytic activity on silicon dioxide nano-wafers using electron beam imaging. The former isn’t much fun and the rewards may be unspectacular but very useful compared to the investment of resources. Now that “Blue Sky” project is really tempting. Company and personal rewards might be astronomical. It might win a Nobel Prize! Nevertheless, it might be nearly impossible to do. Clearly the Research Manager needs to do that library study first and think long and hard about putting resources into that "Blue Sky" project.
Of course, none of the real choices are that clear cut. There are many possible projects and a plethora of resources to manage. There is also the matter of time. Some issues MUST be done very soon while others can wait. The Research Manager needs to budget resources and set priorities based on importance to stakeholders and urgency. The bulk of the Research Budget will be spent on Risk Level 3 issues that are fairly urgent. Here possible solutions seem to exist and reasonable planning can be done to progress toward answering specific questions on specific potential solutions. By driving risk factors from 35% to even 15% there can be a huge change in the value of a technology. The technology can quickly go from one of interest to one of immediate application.
Let’s put some numbers to this. Let’s suppose that we have a project on the books that amounts to spending $2 million on a plant change that might save us $450 thousand per year over the next ten years. At first blush this seems pretty reasonable – a “payout” in 4.5 years. But let’s also suppose that we aren’t very certain of our potential savings. In fact, suppose this is a pretty new technology that we don’t have much experience with and we discount it pretty heavily. Say we even consider it high risk at a 35% discount rate. We would put the PV of these savings at about $1.2 million. We wouldn’t be wanting to spend $2 million to get a PV of $1.2 million unless there was some other driver that is impossible to quantitate (e.g. fixes a known and significant safety hazard). Let’s suppose, however, that we thought we could do a few experiments in our pilot plant to prove out this idea. If we could drive the risk down to around 15% our PV would jump to around $2.3 million. In fact, we could spend up to $300K on evaluating the project and, if successful, we would still be happy. Hence, we could easily justify a $300K research project. Or could we?
Would we actually do the project? Well there was a big “if” in there. How sure are we that we can close the gap? If we were discounting at 35%, we may have some serious concerns that are not easily resolved. Maybe $300K is unlikely to actually solve the problem. We have to convince ourselves that risking dollars today has a good chance of successfully changing the risk/reward dynamic. Furthermore, we have to assess the consequences of investing in this project especially compared to other projects. If $300K is a lot for us to put at risk, we might shelve this project, especially if we had some better cost versus benefit options. On the other hand, if this is the best project opportunity we have and we’ve already sunk a bunch of cost in our R&D budget, we might jump at the chance to prove this out and implement a significant process improvement.
This style of thinking needs to be applied to all the options available to the R&D Group and priorities set. The Research Manager needs to set a master plan/budget at least annually and provide for scheduled review of progress and adjustment. Usually a quarterly review is adequate for most Research efforts.
Rarely can this be effectively done in a vacuum. Research workers and Executives need to participate so that the R&D Group is taking effective action guided by Company priorities and a realistic view of resources. It does no good to work on that which matters not, nor is it prudent to promise results that are completely impossible. Furthermore, the issue of urgency should be overtly discussed. Here broad knowledge of the history of the Company and plans for the coming year can be helpful. A certain fraction of resources should be reserved for the urgent projects that overtake the company. Some will come from the regular course of doing business. Others will come from changes in operations that will generate startup and new problem solving activities that often engage the R&D Group. Anticipating these will improve the overall effectiveness of the R&D Group.
The many options should be categorized as follows:
In general Risk Level 1 (“Low Risk”) projects are often found in the Low Importance/High Urgency quadrant. The returns are not very high, but they are pretty certain and the Company needs to benefit from those returns soon for them to have good value. Nevertheless, these projects cannot squeeze out all other projects just because of their urgency. Only something like 25% of R&D resources should be budgeted for these projects so that projects with High Importance are not ignored.
Risk Level 3 (“Blue Sky”) projects are often found in the High Importance/Low Urgency quadrant. The returns could be great. In fact, they may represent the future of the company, but they may take a long time to develop and prove those returns. They cannot be ignored forever, but they cannot squeeze out all, more urgent projects. Again, budgeting something like 25% of the R&D resources on “Blue Sky” would be great. Often, however, companies just cannot quite get up to that level of commitment. It must not be 0%. If it is, the company is dying.
Level 2 Risk (“Moderate Risk”) projects may or may not be urgent. They tend to have high importance but questions about their risk can reduce their value and urgency. By reducing risk, R&D can make them the “Do Now” project. Here is where the bulk of decision making and R&D effort should be spent (50% and more).
To this point we have focused on financial risks and rewards. Is that all there is to it? Can this be applied to the National Science Foundation, the National Institute of Health, the National Renewal Energy Laboratory and etc.? The answer is a qualified “yes.”
When it comes to comparing alternatives with similar non-monetary benefits the answer is “heck yes.” Spending more money than is needed to achieve an outcome is never justified.
When it comes to placing an absolute monetary value on a social benefit, the issue becomes much foggier. Although it is done, it probably isn’t that useful to try to put a dollar value on saving 20,000 lives per year. Most of the time those data are not very reliable anyway. It seems to me that this approach just encourages voodoo statistics. Probably a more useful approach is to be honest about actual costs and probable beneficial outcomes and let stakeholders decide for themselves in an open, democratic forum. Some will find $200 million spent on a new vaccine for Zika with a small chance of success still a useful investment. Others would much rather see $200 million spent on habitat studies in Africa with a small chance of reversing the decline of the African cheetah. It would be very difficult to calculate the best use of that $200 million. Nevertheless, in an open, vibrant and capital effective society, there would be a much better chance that BOTH programs might be funded to achieve these very diverse social benefits. It is Stalin-like central planning that is more apt to fund high risk missile programs when people are starving.
So to wrap up, the Research Manager should plan the work, budget the work and tie the work to the goals of the organization. These should be actual, formalized, written plans/budgets that are developed with participation from relevant stakeholders. Where practical, goals should be translated into financial measures. We will get more into the specifics of that in later blogs.
Ron Stites holds a BS in Chemistry and an MBA in Finance and Accounting. Stites & Associates, LLC, is a group of technical professionals who work with clients to improve laboratory performance and evaluate and improve technology by applying good management judgment based on objective evidence and sound scientific thinking. For more information see: www.tek-dev.net.
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